{"id": "prb|3|Claude|1", "source": "prb", "split": "test", "paper_id": "prb3", "comment": "The paper's quantitative claims about nuclear quantum effect (NQE) magnitude on proton hopping kinetics rely on MLP-based PIMD simulations that are validated against severely limited DFT PIMD data exhibiting acknowledged non-ergodic sampling behavior.\n\n\"Since performing a full US simulation with 16 beads per umbrella would require a prohibitively large amount of computational resources, the MLP was used to construct an initial FES using a metadynamics simulation, so that the inverse of the obtained FES could be used as bias for the following DFT-US simulations. This allowed us to reduce the number of umbrellas to only 6, with low force constants (~25 kJ·mol⁻¹).\"\nThe DFT PIMD validation uses only 6 umbrellas compared to 39 umbrellas in the MLP simulations, representing a 6.5-fold reduction in sampling coverage. This asymmetry between the validation data and production simulations raises concerns about whether the limited DFT validation can adequately verify the MLP performance across the entire reaction coordinate, particularly in regions critical for computing kinetic rates.\n\"Despite the good overall agreement between the MLP and DFT PIMD profiles, with variations in the order of 5 kJ·mol⁻¹ (Figure S14a), quite some difference can be seen in the steepest regions of the FES (for a collective variable ≈ ±0.7). This is most likely due to the behavior of the DFT umbrellas located in these regions, where clear non-ergodic behavior in the collective variable time series is present (Figure S14b).\"\nThe authors acknowledge that the DFT PIMD simulations exhibit \"clear non-ergodic behavior\" in two umbrellas near the transition state region. This is precisely the region most important for computing reaction rates. While the authors attribute the DFT-MLP discrepancy to DFT sampling issues rather than MLP inaccuracy, the inadequate DFT reference data cannot definitively validate the MLP's quantum free energy predictions, which form the basis for the claimed NQE speedup factors (65x at 273K, 16x at 373K, 7x at 473K).\n\"Given that increasing the number of DFT umbrellas or the simulation time is currently at the edge of our available computational resources, we consider the small differences between the two FESs acceptable given the short time of the DFT simulations and the low error on the forces.\"\nThis statement acknowledges the validation limitations as a computational resource constraint. However, the paper's main conclusions about NQE importance at catalytically relevant temperatures depend critically on the quantum free energy surfaces. Standard practice in MLP-driven PIMD studies, such as in Cendagorta et al. (2021) [[1]](#ref1), typically involves more rigorous validation against DFT PIMD reference data to establish quantitative reliability of NQE predictions.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|3|GPT|1", "source": "prb", "split": "test", "paper_id": "prb3", "comment": "This paper’s quantum Bennett–Chandler rate constant calculation (Section S7.4 and Methods) is methodologically ambiguous and potentially invalid because it appears to propagate thermostatted PIMD trajectories for a quantity that requires an explicit real-time dynamics approximation (e.g., RPMD); this undermines the validity of the reported NQE-induced rate accelerations and derived Arrhenius activation energies.\n\n“PIMD simulations were performed with the i-PI driver\\(^{61}\\) using a time step of 0.25 fs and a PILE thermostat\\(^{62}\\) with a time constant of 100 fs for temperature control.”\nThe manuscript explicitly describes a thermostatted PIMD setup (PILE) for the path-integral simulations, but it does not clearly separate equilibrium sampling (where thermostats are appropriate) from the real-time propagation required in a Bennett–Chandler/reactive-flux transmission coefficient calculation. Because the central quantitative claim (e.g., large speedups like 65× at 273 K) depends on the dynamical recrossing factor, details of the propagation ensemble and thermostatting are not a minor implementation choice. Using thermostatted ring-polymer dynamics corresponds to a different approximation than standard RPMD rate theory, and can change plateau behavior and transmission coefficients. The text therefore leaves it unclear what dynamical approximation is actually being used for the “quantum” rates, which directly affects whether the computed k-values can be interpreted as physical reaction rates. This ambiguity is a major threat to the soundness of the main conclusion because the work’s novelty and message rest on quantitative NQE kinetics rather than only equilibrium free-energy shifts.\n“However, as the sampling protocol of imaginary time PIMD only allows to compute static equilibrium properties and does not allow to compute time-dependent quantities, one needs to resort to approximate techniques such as ring polymer molecular dynamics (RPMD) to calculate quantum real-time correlation functions.”\nThis statement correctly distinguishes equilibrium PIMD sampling from time-dependent correlation functions and rate theory, and it sets an explicit methodological requirement: an approximate real-time dynamics method is needed. Because the paper relies on a Bennett–Chandler style flux–side correlation function for quantum rates, this sentence makes the choice of dynamical approximation central, not optional. It also implies that simply running standard PIMD (with thermostats chosen for sampling) is not sufficient to compute the time-dependent factor in the rate expression. The presence of this sentence makes subsequent descriptions of the actual propagation method especially important to scrutinize. If the authors did not, in practice, switch to RPMD (or a clearly justified alternative), then the reported “quantum” kinetics would not match the stated methodological prerequisites. This discrepancy matters because it would invalidate the claim that the computed rates correspond to quantum real-time kinetics rather than to a sampling artifact.\n“In the centroid formulation, 5,000 configurations with the centroid around the transition state (\\( q^* - 0.05 < q^{(c)}(0) < q^* + 0.05 \\)) were extracted from an US simulation. Similarly to the classical rates (see Section S6.2), a subsequent unbiased PIMD simulation was performed for 50 fs and the rate factor was calculated from Eq. S6.11.”\nAfter explaining that PIMD sampling cannot yield time-dependent quantities and that RPMD is needed, the supplement then describes the actual propagation step as an “unbiased PIMD simulation,” which is inconsistent terminology at best and potentially inconsistent methodology. In common usage, “PIMD” denotes a thermostat-assisted sampling algorithm designed to reproduce equilibrium quantum statistics, not an approximation to real-time quantum dynamics. The manuscript does not clarify whether “PIMD” here is shorthand for an RPMD propagation mode within i-PI, nor does it specify thermostat settings during these 50 fs trajectories. Because transmission coefficients can be sensitive to thermostatting/friction on ring-polymer modes, the lack of a precise description makes it impossible to assess whether the computed plateau reflects an accepted RPMD/BC procedure. This is a major issue because the reported NQE speedups and activation-energy changes are derived from these rates; if the dynamics is not well-defined, the numerical conclusions are not verifiable.\n“It is important to recognize that the classical trajectories have nothing to do with the real dynamics of a quantum system. The dynamics in this isomorphic system simply provides a simple algorithm for simulating the equilibrium properties of the system.” [[1]](https://www.columbia.edu/cu/chemistry/groups/berne/papers/arpc_37_401_1986.pdf)\nThis review statement captures a standard and important limitation: path-integral “dynamics” is not automatically interpretable as quantum real-time dynamics. The paper under review acknowledges this limitation in its supplement, yet still describes its rate-factor trajectories as “PIMD,” creating methodological ambiguity. The quoted sentence emphasizes that without a carefully defined approximate dynamics (e.g., RPMD/TRPMD/CMD), using path-integral trajectories risks producing non-physical dynamical observables. In the context of reaction rates, this directly affects the recrossing factor and therefore the final kinetic constants. As a result, the manuscript must precisely document the chosen dynamics and thermostatting protocol; otherwise, the reported quantitative NQE effects cannot be considered reliable. This is a validity-level concern because the method could, in principle, generate systematically biased rates even if equilibrium free energies are correct.\n“We apply Thermostatted Ring Polymer Molecular Dynamics (TRPMD), a recently-proposed approximate quantum dynamics method, to the computation of thermal reaction rates.” [[2]](https://arxiv.org/abs/1506.07460)\nThis sentence shows that once thermostats/friction are introduced into ring-polymer dynamics, one is no longer in the plain RPMD setting and must treat the approach as a distinct approximation with its own accuracy considerations. The reviewed paper specifies the use of a PILE thermostat for path-integral simulations but does not state whether thermostats are disabled for the rate-factor propagation or whether a TRPMD-like approach is being used instead. Because the accuracy of thermostatted ring-polymer methods for rates is an active methodological question, failing to specify (and justify) which dynamics is used undermines confidence in the reported kinetics. The key point is not that thermostats are always wrong, but that they change the method and must be disclosed and validated. This is especially important here because the main claim is a large, temperature-dependent kinetic effect of NQEs that hinges on the transmission coefficient. Without clarity, readers cannot reproduce or evaluate whether the claimed NQE speedups are robust to method choice.\n\nReferences:\n[1] [Berne, B. J. & Thirumalai, D. “On the Simulation of Quantum Systems: Path Integral Methods.” *Annual Review of Physical Chemistry* 37, 401–424 (1986).](https://www.columbia.edu/cu/chemistry/groups/berne/papers/arpc_37_401_1986.pdf)\n[2] [Hele, T. J. H. & Suleimanov, Y. V. “Should Thermostatted Ring Polymer Molecular Dynamics be used to calculate thermal reaction rates?” arXiv:1506.07460 (2015).](https://arxiv.org/abs/1506.07460)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|3|GPT|2", "source": "prb", "split": "test", "paper_id": "prb3", "comment": "This paper’s calculation of equilibrium site coverages and the overall hopping rate (Supplementary Section S8 and main-text interpretation around Figure 6–7) relies on a least-squares Moore–Penrose solution because the kinetic constants do not yield a unique equilibrium; without enforcing thermodynamic consistency (e.g., detailed balance), this can bias the reported temperature-dependent coverages and thus compromise conclusions drawn from NQE-induced changes in equilibrium populations and Arrhenius activation energies.\n\n“From the 12 kinetic constants characterizing the 6 forward and reverse hoppings between the 4 oxygen atoms in the first coordination sphere of the Al defect, it is possible to compute the equilibrium coverages \\( \\theta_i \\) of each site and, subsequently, the overall hopping rate:”\nThe paper treats equilibrium populations as outputs of the kinetic network built from twelve direction-specific rate constants. In principle, if the underlying dynamics is at equilibrium and rates are thermodynamically consistent, the stationary distribution should be well-defined and should agree with the Boltzmann distribution implied by free-energy differences. However, the manuscript immediately proceeds to an overdetermined least-squares construction, which indicates that the set of estimated rates does not straightforwardly define a unique equilibrium within their numerical uncertainties. Because Figure 6 interprets differences in \\(\\theta_i\\) as physical consequences of NQEs, any numerical procedure that can shift \\(\\theta_i\\) without a thermodynamic constraint is a threat to the paper’s central interpretation. This is not merely an implementation detail: \\(\\theta_i\\) directly enters the overall hopping rate and thus the Arrhenius slope reported as an “effective activation energy.” If \\(\\theta_i\\) is biased by the fitting procedure, then both equilibrium conclusions and kinetic conclusions downstream can be distorted.\n“which immediately yields \\( \\theta_4 = 1 - \\sum_{n=1}^{3} \\theta_i \\). This leaves us with 4 equations, one for each oxygen site, in 3 unknowns (\\( \\theta_1, \\theta_2 \\) and \\( \\theta_3 \\)). Because of the uncertainties on the kinetic constant, the system does not have a unique solution. The least squares solution can be found using the Moore-Penrose inverse coefficients matrix:”\nThis passage explicitly states that the equilibrium problem is not uniquely solvable with the computed kinetic constants and that a Moore–Penrose least-squares solution is imposed. That choice effectively defines a “best fit” stationary distribution even when the rates are not mutually consistent, which can occur when forward/backward rates violate thermodynamic constraints beyond statistical noise. The manuscript does not report enforcing detailed balance or constraining the rates so that equilibrium fluxes are exactly balanced for each elementary hop, which is the standard expectation for equilibrium kinetics in closed systems. The authors do check that residuals are small, but small residuals only indicate that the fitted \\(\\theta\\) approximately satisfies the linear system; they do not guarantee thermodynamic correctness or uniqueness of the implied equilibrium state. Because the paper’s discussion attributes qualitative physical meaning to differences in \\(\\theta_3\\) versus \\(\\theta_1\\) under NQEs, the equilibrium-computation procedure itself must be demonstrably robust and physically constrained. Without that, the conclusion that NQEs “change the computed equilibrium proton coverages” could partly reflect how inconsistencies in noisy rates are resolved.\n“\\[ r_{hopping} = \\sum_{i=1}^{4} \\sum_{j \\neq i}^{4} k_{ij} \\theta_j, \\]”\nThe supplementary presents a formula for the overall hopping rate that weights outgoing rates \\(k_{ij}\\) by \\(\\theta_j\\), whereas the main text elsewhere uses the more standard outgoing-flux form \\(\\sum_{i} \\sum_{j\\neq i} k_{ij}\\theta_i\\). Even if this is only a typographical error, it exemplifies that the derivation of the overall rate and its dependence on \\(\\theta\\) is not presented with enough clarity to ensure readers can reproduce the reported Arrhenius trends. In a multi-state network, swapping \\(\\theta_i\\) and \\(\\theta_j\\) changes the physical meaning (reactant-state occupancy versus product-state occupancy) and can materially change the computed net event frequency. Given that the manuscript’s headline quantitative outcomes include specific speedup factors and activation energies, such ambiguity in the governing equation is significant. This also reinforces the need for a thermodynamically constrained and transparently documented post-processing pipeline for \\(\\theta\\) and \\(r\\). Without it, the mapping from microscopic rate constants to macroscopic hopping rates is not reliably verifiable.\n“Once all the equilibrium coverages as a function of temperature are known, the overall hopping rate can be computed using the formula:\n\n\\[\nr = \\sum_{i=1}^{4} \\sum_{j \\neq i}^{4} k_{ij} \\theta_i,\n\\]”\nThis main-text definition of the overall hopping rate uses reactant-state coverages \\(\\theta_i\\) to weight outgoing hopping rates \\(k_{ij}\\), which is the standard form for counting events per unit time. In the Supplementary Information, however, the corresponding formula weights \\(k_{ij}\\) by \\(\\theta_j\\), creating an internal inconsistency in the manuscript’s definition of the reported macroscopic rate. Because the Arrhenius plots and activation energies are computed from this overall hopping rate, any ambiguity about whether \\(\\theta_i\\) or \\(\\theta_j\\) is used is materially significant. If the two expressions were both evaluated, they would generally give different numerical rates except in special symmetric cases, so this cannot be dismissed as a cosmetic issue without showing the implementation. The inconsistency also compounds the concern that the downstream rate/coverage pipeline is not sufficiently transparent to verify from the paper alone. Clarifying the exact implemented formula and providing the corresponding analysis code would be necessary to ensure the derived rates and activation energies are reproducible and correctly interpreted.\n“In thermodynamics, the principle of detailed balance says that every process of energy transfer in one direction must also allow energy transfer in the opposite direction, and in equilibrium, the flux in both directions must be equal.” [[3]](https://en.wikipedia.org/wiki/Detailed_balance)\nThis definition states the equilibrium expectation that forward and reverse elementary processes balance, which is the physical basis for deriving equilibrium populations from reversible kinetics. If a set of estimated \\(k_{ij}\\) does not satisfy such balance (even approximately), then any computed “equilibrium coverages” depend on how inconsistencies are resolved rather than being uniquely implied by the physical model. The supplement’s admission that the system “does not have a unique solution” suggests that such inconsistencies exist at the level of the reported rate estimates and propagated uncertainties. A common remedy is to enforce detailed balance (or otherwise enforce reversibility constraints) when estimating rates or when computing the stationary distribution, so that equilibrium populations are thermodynamically grounded. The manuscript does not describe such enforcement, but instead applies a Moore–Penrose least-squares procedure that can, in general, yield different \\(\\theta\\) than a thermodynamically constrained approach. Because the paper’s interpretation of NQEs depends on the differences between classical and quantum \\(\\theta\\), this omission affects the reliability of the conclusions.\n\nReferences:\n[3] [“Detailed balance.” *Wikipedia* (accessed via extracted page).](https://en.wikipedia.org/wiki/Detailed_balance)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|3|GPT|3", "source": "prb", "split": "test", "paper_id": "prb3", "comment": "This paper’s conclusions about MLP transferability beyond H-CHA (main text Discussion and Supplementary Section S9) are not adequately supported for the target phenomenon (proton hopping kinetics) because the transferability tests are performed only on all-silica frameworks without hydrogen and without Brønsted acid sites; this weakens the robustness and significance of claims about extending the approach to other zeolite topologies.\n\n“To broaden our scope, it is important to assess the MLP capability of describing other zeolite frameworks on which the MLP was not trained. To this end, the transferability of the MLP to other zeolite topologies was investigated.”\nThe manuscript frames transferability as a key step toward broader applicability beyond the specific H-CHA case study, which is central to the work’s significance claim as a proof-of-concept for heterogeneous catalysis. However, “transferability” is only meaningful relative to the target tasks—here, reactive proton hopping around an Al defect with NQEs. If the performed validation does not include that reactive chemical environment, it cannot substantiate transferability for the main scientific quantity of interest (reaction kinetics). This matters because the conclusions invite readers to believe that only limited additional training is needed for other frameworks, which is a strong practical implication. Without reactive-site tests, the presented evidence only supports that the MLP is numerically stable on related silica frameworks, not that it is accurate for proton transfer barriers, recrossing factors, or tunneling-sensitive dynamics. As such, the transferability component does not robustly support the paper’s broader generalization.\n“To obtain an indication of the capability of the MLP to model other zeolite frameworks, the all-silica structures of CHA, AFX, FER, MFI and MOR were obtained from the IZA zeolite database [55].”\nThis sentence makes explicit that the transferability test systems are all-silica frameworks, which exclude both the Al substitution and the Brønsted proton central to the paper’s chemistry. Because the MLP is trained to reproduce a reactive PES involving O–H bond breaking/forming near Al, evaluating it only on Si–O–Si network dynamics does not probe whether it generalizes to different acid-site geometries or proton-binding motifs. This is particularly important because proton transfer rates can be highly sensitive to local electrostatics and short-range interactions, not merely to the stability of the silica lattice. Therefore, while the test may demonstrate that the potential is not catastrophically unstable outside its training topology, it does not validate the claimed capability to model proton hopping in other zeolites. The manuscript’s broader implications would require at least some reactive-site test cases (even a small number) to be convincing. Without them, the conclusions about applicability beyond H-CHA are substantially overstated relative to the evidence.\n“Because of the lack of hydrogen atoms, the time step was increased to 1 fs.”\nThis explicit acknowledgment confirms that hydrogen is absent in the transferability simulations, which means the validation does not cover the very degrees of freedom for which NQEs and tunneling are being claimed as critical. Since the paper’s main message is about NQEs on proton hopping kinetics, excluding hydrogen from the transferability tests disconnects the validation from the core phenomenon. It also means the test cannot reveal whether the MLP’s learned description of O–H interactions extrapolates sensibly in other frameworks or near different T-site environments. Moreover, a potential can behave “reasonably physical” for a silica lattice while being substantially wrong for reactive proton dynamics, because these are different regions of configuration space and involve different interaction scales. Consequently, the reported “moderate” force errors on silica atoms cannot be used as evidence that proton hopping kinetics would be reliable elsewhere. This limits the interpretability of the transferability section as support for broader catalytic applications.\n“Unfortunately, explicitly testing the proton hopping transferability would require additional expensive DFT US simulations and was therefore not further investigated.”\nThis sentence concedes that the work does not actually test transferability for the proton hopping reaction itself, which is the central scientific target. While it is reasonable that additional DFT-US data is costly, the absence of such tests means that any transferability implication for reactive kinetics remains speculative. Because the paper positions the approach as opening a “window” to systematic inclusion of NQEs in heterogeneous catalysis, the strength of that claim depends on whether one can expect the trained MLP to generalize across frameworks or whether each new system requires substantial retraining and validation. The text provides no quantitative evidence (e.g., reactive barriers, proton localization energetics, or NQE-sensitive rate factors) in other topologies to support the implication. As a result, the conclusions about extending to other zeolite frameworks are not adequately supported by the presented validation. This affects the perceived significance and generality of the methodology.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|3|GPT|4", "source": "prb", "split": "test", "paper_id": "prb3", "comment": "This paper does not provide sufficiently detailed and accessible materials to reproduce the reported MLP/PIMD kinetics (notably the 0.6 μs aggregate path-integral sampling and the Bennett–Chandler rate calculations) because key analysis components are in-house (ThermoLIB) and broader data are “available upon request”; additionally, the provided code materials do not constitute an executable pipeline for reproducing the MLP training and kinetic analysis.\n\n“The bias potential was applied using PLUMED\\(^{48,49}\\) and the final statistical analysis of the data was performed with our in-house developed ThermoLIB library.\\(^{50}\\)”\nThis statement indicates that a core part of the computational workflow—turning raw umbrella-sampling and rate trajectories into final free-energy surfaces, rates, and uncertainties—depends on a non-public in-house library. In computational chemistry, reproducibility typically requires that analysis scripts and post-processing steps be available, because small choices (reweighting, error estimation, histogram/binning, convergence criteria) can materially affect reported barriers and rates. The paper’s main claims hinge on quantitative differences in kinetic constants and derived activation energies across temperatures, so the analysis layer is not ancillary. Without access to ThermoLIB (or an explicit, complete reimplementation specification), independent researchers cannot verify the correctness of the reported numbers or reproduce them from the same trajectories. This is especially problematic given that the authors also note non-ergodicity issues in some DFT PIMD umbrellas, which increases the importance of transparent reweighting and uncertainty estimation. Therefore, the in-house dependency is a major barrier to reproducibility.\n“Relevant atomic coordinates, example of input files and the trained MLP can be found in the Supplementary Data. Any other data is available from the authors upon reasonable request.”\nThe manuscript’s data availability statement does not commit to releasing the full set of artifacts needed to reproduce the study, especially the large DFT-US training dataset, complete simulation inputs for all temperatures/hopping paths, and the full analysis workflow. “Available upon reasonable request” is widely recognized as insufficient for reproducible computational science because access can be delayed, denied, or incomplete, and it prevents automated reanalysis. Here, the core results (e.g., temperature-dependent quantum rates for 12 directions over 7 temperatures) depend on numerous simulation and analysis choices that are difficult to reconstruct from narrative description alone. The paper claims that key items exist in “Supplementary Data,” but the reproducibility standard for such a complex workflow would require a persistent, versioned archive containing all inputs, trained weights, and scripts. Given the centrality of machine-learning potentials, even small changes in training splits, hyperparameters, or reference-energy handling can change dynamics and rates, so releasing “examples” is not enough. This materially affects whether the reported kinetics can be independently validated.\n```text\n  # CP2K\n\n  CP2K is a quantum chemistry and solid state physics software package that can perform atomistic\n  simulations of solid state, liquid, molecular, periodic, material, crystal, and biological systems.\n  CP2K provides a general framework for different modeling methods such as DFT using the mixed\n  Gaussian and plane waves approaches GPW and GAPW.\n  ```\nThe code materials included with the submission consist of the CP2K source tree and general CP2K documentation, which does not constitute a reproducible pipeline for this specific paper’s MLP training, umbrella sampling setup, ring-polymer simulations, or Bennett–Chandler rate analysis. While CP2K is indeed the DFT engine used, reproducing the paper requires precise CP2K input decks (basis sets, pseudopotentials, thermostat settings, cell equilibration protocol, PLUMED bias definitions, wall potentials), plus the training and inference code for SchNetPack and the coupling to YAFF and i-PI. The provided CP2K repository alone cannot recreate the authors’ simulation campaign or the trained MLP without the missing experiment-specific inputs and datasets. This mismatch between what is needed (a full workflow) and what is provided (a general-purpose electronic-structure package) creates a substantial reproducibility gap. Because the paper’s central message is about enabling large-scale PIMD kinetics via MLPs, the absence of an executable, end-to-end workflow is not a minor omission. It prevents independent verification of both the ML fidelity claims and the final kinetic conclusions.\n“All scholarly digital research objects—from data to analytical pipelines—benefit from application of these principles, since all components of the research process must be available to ensure transparency, reproducibility, and reusability.” [[4]](https://www.nature.com/articles/sdata201618)\nThis statement articulates a widely accepted standard for computational reproducibility: not only raw data, but also the workflows and tools that transform data into results must be available. In the reviewed manuscript, several essential components are not provided as durable, public research objects, notably the in-house ThermoLIB analysis and the full set of simulation inputs and training data underlying the MLP. The study’s complexity (multiple temperatures, multiple hopping paths, classical vs quantum workflows, and time-correlation based rate computations) makes it impractical to reproduce from prose alone. Therefore, the paper falls short of current community expectations for reusable computational research outputs, particularly for machine-learning-driven simulation studies. This is not simply about convenience; it affects the ability of other researchers to validate the magnitude and temperature range of the claimed NQE effects. The FAIR principles highlight that full transparency requires sharing the end-to-end pipeline, which is not met here.\n“Yaff stands for “Yet another force field”. It is a pythonic force-field (FF) code used at the Center for Molecular Modeling (CMM) to test-drive new FF models.” [[5]](http://molmod.github.io/yaff/index.html)\nThe manuscript indicates that YAFF is used as part of the classical MLP simulation workflow, but the paper does not provide the exact YAFF interfaces, driver scripts, or coupling code used to run the SchNet potential in production MD/US and to generate the ensembles used for rate computations. In complex multi-code workflows, reproducibility depends on the glue code and the precise versioning/configuration of each component, not just on naming the packages. The YAFF documentation shows it is a general codebase rather than a paper-specific artifact; therefore, citing YAFF does not substitute for releasing the exact scripts and settings used. This is especially important when combining YAFF with PLUMED biases and i-PI for path integrals, where implementation choices can materially affect sampling and kinetics. Consequently, the methodology remains underspecified for independent reproduction even if all upstream simulation engines are publicly available. This reinforces the reproducibility concern raised by the reliance on in-house ThermoLIB and “available upon request” data.\n\nReferences:\n[4] [Wilkinson, M. D. et al. “The FAIR Guiding Principles for scientific data management and stewardship.” *Scientific Data* 3, 160018 (2016).](https://www.nature.com/articles/sdata201618)\n[5] [“Yaff Documentation — Yaff 1.4.2 documentation.” (YAFF project documentation site).](http://molmod.github.io/yaff/index.html)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|3|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb3", "comment": "The authors employ the PBE functional (a Generalized Gradient Approximation, GGA) for the underlying DFT calculations without sufficient validation against higher-level methods, despite the known tendency of GGAs to significantly underestimate proton transfer barriers.\n\n\"The PBE functional [53] was used in combination with the D3 dispersion corrections [55].\" (from Supplementary Information, Section S3.1.1)\nThe authors explicitly state the use of the PBE functional. It is well-established in the literature that GGA functionals like PBE suffer from self-interaction error, which often leads to a systematic underestimation of reaction barrier heights, particularly for proton transfer reactions.\n\"Periodic DFT, B3LYP/T(O)DZP, static... 69 [kJ/mol]\" (from Supplementary Information, Table S1, citing Ref [1])\nThe authors' own compilation of literature values shows that hybrid functionals (like B3LYP) yield activation energies around 69 kJ/mol.\n\"Periodic DFT+MP2 corrections (+ZPE), static... 65 [kJ/mol]\" (from Supplementary Information, Table S1, citing Ref [3])\nSimilarly, methods including MP2 corrections suggest barriers around 65 kJ/mol. In contrast, while the specific PBE barrier values are not explicitly tabulated in the text, the visual representation in Figure 4 and Figure S10 suggests values in the range of 40-50 kJ/mol (consistent with typical GGA underestimation). This discrepancy of ~15-20 kJ/mol would lead to errors of several orders of magnitude in the calculated rate constants, undermining the paper's claim of deriving accurate kinetics.\n\nReferences:\n[1] [Goncalves, T. J., Plessow, P. N. & Studt, F. On the Accuracy of Density Functional Theory in Zeolite Catalysis. ChemCatChem 11, 4368–4376 (2019)](https://doi.org/10.1002/cctc.201900778)\n[3] [Cohen, A. J., Mori-Sánchez, P. & Yang, W. Insights into current limitations of density functional theory. Science 321, 792–794 (2008)](https://doi.org/10.1126/science.1158722)", "reviewer_type": "ai", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|3|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb3", "comment": "The authors fail to provide the specific datasets (training structures) and input scripts necessary to reproduce the Machine Learning Potential (MLP) training and the subsequent Path Integral Molecular Dynamics (PIMD) simulations.\n\n\"Energies and forces were extracted every 5 fs from the DFT US trajectories, yielding a total of ~1,200,000 training structures which were used to train an MLP with the SchNetPack package\" (from Supplementary Information, Section S5.1)\nThe training dataset of ~1.2 million structures is a critical component of the work. Without access to this specific dataset, it is impossible for other researchers to reproduce the MLP or verify its quality.\n\"CP2K is a quantum chemistry and solid state physics software package...\" (from `code/README.md` in the provided repository)\nThe provided `code` directory contains the standard source code for the CP2K software package but lacks the specific input files (e.g., for the H-CHA system, the specific umbrella sampling parameters, or the MLP training scripts) required to replicate the study. Providing the generic software source code without the specific simulation inputs does not satisfy the requirement for reproducibility.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|3|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb3", "comment": "The practical significance of the findings for zeolite catalysis is not clearly demonstrated, as the \"significant impact\" of NQEs is claimed only for temperatures up to ~473 K, which is below the typical operating range for many zeolite-catalyzed reactions.\n\n\"NQEs are found to significantly impact the proton hopping kinetics up to ~473 K.\" (from Main Paper, Abstract)\nThe authors highlight the significance of NQEs up to 473 K. However, many industrial zeolite processes, such as the Methanol-to-Olefins (MTO) conversion, operate at temperatures significantly higher (e.g., >600 K).\n\"While the work performed here is illustrative for the most basic proton hopping reaction in zeolites, it paves the way towards a routine inclusion of NQEs...\" (from Main Paper, Introduction)\nWhile the methodological contribution is noted, the specific scientific conclusion regarding the impact of NQEs on proton hopping appears to be of limited relevance for actual catalytic conditions if the effect vanishes at operating temperatures. The manuscript would benefit from a more explicit discussion of the magnitude of NQEs at these higher temperatures to contextualize the significance of the results.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|3|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb3", "comment": "Catalytic reactions with zeolites are often carried out at temperatures higher than 473 K, so the authors should explain, which type of reactions they think are candidates to be affected by this.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|3|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb3", "comment": "The activation barrier for the proton hopping process is 55.8 kJ/mol (Figure 7a), and it is 11 kJ/mol higher without quantum effects. Previous calculations without considering the quantum nature of the protons generally yielded higher activation barriers than reported here (Figure 1b, CHA). However, experimental values from the literature are lower. So, there is a discrepancy between the value obtained here and the experimental data in the literature. The authors claim that it is almost impossible to obtain a fully dehydrated zeolite, and this seems to be the explanation they offer. A solid-state NMR paper by Huo et al is cited to make this statement (reference 19). Those authors indeed declare that they had water contamination. It is absolutely important for 1H solid-state NMR of zeolite acid sites to employ an advanced sample handling procedure, and this has been shown frequently. On the other hand, Franke and Simon have shown (by impedance measurements) that the proton conductivity only goes up dramatically, when there is a water chain between two sites to allow the Grotthus mechanism. Another question is, how trace amounts of water that are far away would affect local proton hopping. In-situ infrared spectroscopy is somewhat easier because those experiments use self-supporting zeolite wafers in an in-situ cell, where the zeolite can be dried while studied. For example, a more recent paper by Losch et al. (JACS 2018) reports an activation barrier of 40 kJ/mol. Therefore, after decades of experimental work on zeolite acid sites, this seems to be a sweeping judgement to say that none of those materials was sufficiently dry to hold up with these new calculations. Experimental work – by nature – deals with real materials, and yes, it is true, sometimes with water contaminations, but there are other factors, such as Si/Al ratio or defect sites, or site distributions. Therefore, there is a lack of an equal and fair comparison of the results for real materials and the ideal model structure used in this work.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|3|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb3", "comment": "The authors argued the very low experimental barriers for the proton hopping are most likely related to the humid environment of zeolites. Does the MLP work for this case? For example, put a couple of water molecules around the BAS to study its effects on the barrier of proton hopping.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|3|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb3", "comment": "The reason for the high temperature leading to large barrier (as shown in Figure 3 and Figures 15-16) should be clarified properly.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|3|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb3", "comment": "Figure S8 shows that the force MAE goes down with the increasing training time. However, it looks like that it is acceptable after 30h. Did the authors consider the over training problem in the machine learning process?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|3|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb3", "comment": "Can the trained MLQs be tabulated as separately files? Hence, these file can be channeled to other MD engines such as LAMMPS. At least, these potential files should be provided in the supporting information.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|3|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb3", "comment": "In the MLQs based molecular dynamics simulations, is there a scheme to pick outliers which is not sampled in the AIMD/PIMD and appears in the MLQs based molecular dynamics simulations? Is the MLQs refined in the MLQs based molecular dynamics simulations?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|3|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb3", "comment": "Figure S9, x-label (d(H,Oi)) and y-label(d(H,Oj)) is inconsistent with that in Eq. S5.9. they should be r(H,Oi) and r(H,Oj).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|3|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb3", "comment": "It is unclear to the reader why high-temperature simulations were performed at 873 K, what is special about this temperature?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|3|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb3", "comment": "1. This sentence is a bit disturbing: \\\"Surprisingly, not only did none of the MLP simulations presented obvious instabilities, but the error on the forces also remains moderate for frameworks that do not share any secondary building unit with CHA, varying between 196 meV·Å-1 for MOR and 258 meV·Å-1 for MFI. T\\\" Not blowing up should hardly be considered a success for a ML potential and errors of 200 meV/A are quite high and mayeven lead to qualitatively wrong results. RDFs are a nice unit test but also usually fairly easy to get right. While improving this may require more fundamental advances in ML potentials, I believe the language should be adjusted here.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|3|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb3", "comment": "Reproducibility: it would be great to give details on the Nose-hoover thermostat, in particular the Nose mass.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|3|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb3", "comment": "Data availability: this work has amassed a large amount of DFT data, these should be publicly shared and documented well, not only be made available upon request! The same goes for the trained potential files and all input files. Much of the progress achieved in this work would be put to waste if these data are not published.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|3|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb3", "comment": "The authors go to considerable length via computational means (see comments below) to elaborate the possibility of NQEs affecting the rates and Arrhenius-like behavior of proton hopping across several sites in zeolites. They conclude that at room temperature and even at higher industrially relevant temperature NQEs may be important, i.e., up to a factor as large as ten or more at the lower temperatures. The issue here, however, is that a NQE (the quantum enhancement relative to classical mechanics) is not an experimentally measurable quantity since classical mechanics does not exist in reality. What is a measurable quantity would be a kinetic isotope effect (substitution of H by D), but these authors do not seem to calculate this. In turn, this effect is something that could be measured experimentally in principle. As such, these calculations are more of a novelty of interest to the theory community but not of relevance to a broader audience because the NQEs cannot be measured directly (it is not possible).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|3|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb3", "comment": "Another angle that might justify publication in Nature Comm would be the novelty of a computational approach, in this case the use of machine learning to train a potential energy surface from electronic DFT calculations, and to then use that ML surface in more extensive simulations (in this case path integral MD, or PIMD). Unfortunately, this idea is not new and it is being done quite a bit (recent work by Roberto Car on liquid water published in PNAS comes to mind). Moreover, by using a ML potential in another way, it is now possible to do highly efficient direct ab initio MD (AIMD) calculations with PIMD for the NQEs [see Li and Voth, J. Chem. Theory Comp. **18**, 599-604 (2022)]. This was not done.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|3|Human_3|7", "source": "prb", "split": "test", "paper_id": "prb3", "comment": "Additionally, there are questions of accuracy in the computational ML potentials fit to DFT. It seems the error between the DFT and the ML potential derived barriers (Fig 4) are about \\( 2\\ k_B T \\) which is not negligible in an exponential Arrhenius factor (a factor of ~7 in rate), perhaps giving an error as large at the NQE itself in some cases. Also, the ML potential is trained to classical DFT (AIMD) calculations at a high temperature. It not clear that classical simulations at a high T explore some of the regions of the potential that a nuclear quantized system would do (classically “forbidden” regions), so it is not clear that the ML PIMD would give the same behavior as ab initio PIMD. For liquid water this is not the case that classical high-T is like a NQE at lower-T (see C. Li, et al, , J. Chem. Theory Comp. **18**, 2124-2131 (2022)).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|3|Human_3|8", "source": "prb", "split": "test", "paper_id": "prb3", "comment": "Two other points of clarification. First, the idea of using the imaginary time Feynman path centroid in a quantum TST as done in the authors’ Eq. (S7.17) certainly did not originate with them nor with Manolopoulos. The earliest reference in that regard would be Voth, et al, J. Chem. Phys. **91**, 7749-7760 (1989) which should be cited along with some related earlier work by Gillan cited therein. Secondly, for calculating the quantum “dynamical” effects via a classical-like Bennett-Chandler formula, the authors appear to use the ad hoc RPMD approach. Here it should be clarified that RPMD is ad hoc and has no real theoretical justification in terms of actual quantum dynamics [see S. Jang, A. V. Sinitskiy, and G. A. Voth, J. Chem. Phys. **140**, 154103 (2014)]. PS-The authors should also not claim that the so-called “Matsubara dynamics” of Althorpe somehow “derives” RPMD as it does not. Matsubara dynamics is also quite approximate and one cannot really derive one approximation from another.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Claude|1", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "The paper's title and abstract claim the model predicts TS structures for \"general chemical reactions\" and \"general organic reactions,\" but the training and evaluation exclusively use the Grambow dataset which contains only gas-phase unimolecular reactions with small molecules (up to 7 heavy atoms, CHNO only). This represents a narrow subset of organic chemistry that does not support the generalization claims.\n\n* Quote (Title and Abstract): \"Prediction of Transition State Structures of General Chemical Reactions via Machine Learning\" and \"Herein, a novel machine learning (ML) model for predicting TS structures of general organic reactions is proposed.\"\nThe term \"general\" strongly implies broad applicability across diverse reaction types, molecular sizes, and chemical systems. However, the model was trained and evaluated exclusively on unimolecular gas-phase reactions with molecules containing at most 7 heavy atoms. This is a highly restricted chemical space that excludes bimolecular reactions, solution-phase chemistry, larger molecules common in pharmaceutical and industrial applications, and elements beyond C, H, N, and O.\n\"The proposed model is trained and validated using the organic reaction database released by Grambow et al.\"\nThe Grambow database, as described in the original publication, contains reactions generated from molecules selected from GDB-7 (molecules with at most 7 heavy atoms). The database specifically states \"All reactions are gas-phase calculations involving up to seven carbon, oxygen, or nitrogen atoms per molecule.\" This severely limits the chemical diversity and molecular complexity represented in the training data.\n\n* Quote from Grambow et al. [[1]](#citation-list): \"We only considered molecules with at most seven heavy atoms (C, N, O). All molecules with six or fewer heavy atoms were selected from GDB-7 (~770) and a random selection of ~430 molecules were selected from the set with seven heavy atoms.\"\nThe original dataset paper explicitly acknowledges the small molecule limitation. Drug molecules, natural products, and industrial chemicals typically contain 20-50 or more heavy atoms and include elements like halogens, sulfur, and phosphorus. Without evaluation on such systems, claims about \"general\" chemical reactions are not substantiated.\n\n* Quote from TSNet paper (Jackson et al.) [[2]](#citation-list): \"TSNet is presented, a new end-to-end Siamese message-passing neural network based on tensor field networks shown to be capable of predicting transition state geometries. Also presented is a small dataset of SN2 reactions which includes transition state structures.\"\nEven the comparison method TSNet recognized the need to evaluate on different reaction types (SN2 reactions) beyond the Grambow dataset. The present paper does not demonstrate generalization to out-of-distribution reaction types or larger molecules, yet makes stronger claims about generality.\n\nReferences:\n[1] [Grambow, C.A., Pattanaik, L. & Green, W.H. Reactants, products, and transition states of elementary chemical reactions based on quantum chemistry. Sci Data 7, 137 (2020).](https://www.nature.com/articles/s41597-020-0460-4)\n[2] [Jackson, R., Zhang, W. & Pearson, J. TSNet: predicting transition state structures with tensor field networks and transfer learning. Chem. Sci. 12, 10022–10040 (2021).](https://pubs.rsc.org/en/content/articlelanding/2021/sc/d1sc01206a)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Claude|2", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "Intrinsic Reaction Coordinate (IRC) calculations, which are the gold standard for verifying that a transition state connects the correct reactant and product, were performed only on the 126 cases with energy errors greater than 0.1 kcal/mol. This represents approximately 11% of the test set, leaving 89% of predictions without rigorous chemical validation of their connectivity.\n\n\"Intrinsic reaction coordinate (IRC) calculations are performed for the structures on right side of the red bar (126 cases).\"\nFigure 4 shows that IRC calculations were performed only for structures with energy errors exceeding 0.1 kcal/mol. While these are the higher-error cases, chemical validity requires confirming that a TS structure actually connects to the intended reactant and product through IRC calculations. Without IRC verification, a structure with low energy error might still correspond to a different reaction pathway or be a different conformer of the TS. The 88.8% of cases below 0.1 kcal/mol were not IRC-validated.\n\"88.8% of the optimization results have energy errors of less than 0.1 kcal/mol.\"\nWhile low energy error is encouraging, it does not guarantee chemical validity. A predicted TS structure that optimizes to a low-energy saddle point might represent a different elementary step than the reference reaction if the IRC path connects to different products. Standard practice in computational chemistry, as noted in multiple references, requires IRC calculations to confirm that transition states connect to the correct minima.\n\n* Quote from standard computational chemistry practice [[3]](#citation-list): \"Intrinsic reaction coordinate (IRC) calculations were executed to confirm that transition states connect two relevant minima.\"\nThe computational chemistry literature consistently emphasizes IRC calculations as essential validation for transition states. By performing IRC on only 11% of the test cases, the paper cannot claim that 93.8% of predictions are chemically valid—only that they converge to saddle points and have reasonable energies.\n\"Distributions of absolute energy errors of structures whose reference product and reactant structures are acquired (orange) or not acquired (blue) by IRC calculations.\"\nEven among the IRC-validated cases, Figure 4(c) shows that some structures failed to recover the reference reactant and product, indicating that even converged structures with certain energy errors can correspond to incorrect reaction pathways. This reinforces the need for comprehensive IRC validation across all test cases.\n\nReferences:\n[3] [Unveiling the Origins of Enantioconvergence in Cobalt-Catalyzed Reactions - ACS Catalysis (2025)](https://pubs.acs.org/doi/10.1021/acscatal.5c06147)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Claude|3", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "The paper claims that TSGen and TSNet were \"trained with the same database,\" but provides insufficient details about whether these re-implementations faithfully reproduce the original methods, particularly regarding TSNet's transfer learning protocol which was identified as important for its performance.\n\n\"To compare the performances against the other ML models, two existing models, TSGen and TSNet, are trained with the same train dataset.\"\nThe paper states that comparison models were retrained but does not specify the hyperparameters used, whether the original architectures were exactly reproduced, or the source of the implementations. Both TSGen and TSNet papers provide specific details about their architectures and training that would need to be carefully followed for a fair comparison.\n\"Both comparison models are trained with the same database as the database used for training of the proposed model.\"\nWhile using the same database is necessary for fair comparison, it is not sufficient. TSNet in particular relies on transfer learning from equilibrium molecular structures (the ANI-1 dataset) to improve its performance on transition states. If this pretraining step was omitted, the comparison would be unfair to TSNet.\n\n* Quote from TSNet paper (Jackson et al.) [[2]](#citation-list): \"Finally, transfer learning, a low data remedial technique, is explored to understand the viability of pretraining TSNet on widely available chemical data may provide better starting points during training, faster convergence, and lower loss values.\"\nThe TSNet paper explicitly emphasizes transfer learning as a key component of their approach. The present paper does not mention whether TSNet was pretrained on equilibrium structures before fine-tuning on transition states. If transfer learning was not performed, the reported ~15% error for TSNet on bond-forming/breaking pairs (versus ~5% for the proposed method) may not represent TSNet's full capability.\n\"TSGen exhibited slightly better performance than TSNet. However, both models showed more than two-fold greater errors (for both error metrics) compared with the proposed model.\"\nThe claim of two-fold improvement is significant but requires validation through independent replication. Without access to the actual code used for training or detailed hyperparameter specifications, the community cannot verify these comparisons.\n\nReferences:\n[2] [Jackson, R., Zhang, W. & Pearson, J. TSNet: predicting transition state structures with tensor field networks and transfer learning. Chem. Sci. 12, 10022–10040 (2021).](https://pubs.rsc.org/en/content/articlelanding/2021/sc/d1sc01206a)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Claude|4", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "The paper employs 90 trained models for ensemble predictions, which substantially increases computational resources and inference time, yet provides no systematic ablation study showing how performance scales with ensemble size or whether fewer models could achieve comparable results.\n\n\"For the ensemble predictions, 90 trained models are employed.\"\nUsing 90 models represents a very large ensemble that likely requires 90× the inference computation compared to a single model. While ensembles are known to improve accuracy, such a large number is unusual and warrants justification through an ablation study showing the marginal benefit of additional models.\n\"Six different combinations of c and c' in Equation 5 are used to train the model and three independent training with different random seeds are performed for every combination of c and c'. Although all the hyperparameters are identical, depending on the random seed, ML model are differently trained. For each training, five best models are saved and used for the ensemble predictions.\"\nThe ensemble construction methodology (6 hyperparameter settings × 3 random seeds × 5 saved models = 90 models) is described, but the paper does not analyze how much each factor contributes to the final performance. It is unclear whether using fewer hyperparameter settings, fewer random seeds, or fewer saved models per training would substantially degrade performance.\n\"The error of the outputs of the single-model and ensemble include 3.681% and 3.407% (molecular MAPE), respectively, and 11.56pm and 10.70pm (molecular MAE), respectively.\"\nThe improvement from single model to 90-model ensemble is relatively modest (~8% relative reduction in MAPE). Given the 90× increase in inference cost, a systematic study of performance vs. ensemble size would help users make informed decisions about the accuracy-efficiency tradeoff. Such ablation studies are standard practice in ensemble learning literature to demonstrate the value proposition of increased computational investment.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|GPT|1", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "This paper’s primary chemical-validity conclusions (Validity, Conclusions) are not sufficiently supported because the main validation metric is saddle-point optimization convergence and energy agreement, while explicit pathway/connectivity verification (via IRC) is applied only to a small, biased subset; therefore the reported 93.8% “success ratio” does not reliably establish that predicted TS structures correspond to the intended reactant–product transformation.\n\n“The predicted TS structures result in a high success ratio (93.8%) of quantum chemical saddle-point optimizations, and 88.8% of the optimization results have energy errors of less than 0.1 kcal/mol.”\nThis sentence elevates convergence rate and a very tight energy-difference threshold to headline evidence of correctness, but neither metric alone establishes that the optimized saddle point connects the intended reactant and product. A TS optimization can converge to an unintended saddle point (e.g., a different reaction channel or a conformational TS) while still achieving a stable first-order saddle point. Likewise, an energy close to a reference TS does not guarantee the same intrinsic reaction pathway or correct connectivity. In transition-state methodology, chemical validity is normally tied to whether the TS connects the target minima on the potential energy surface. Because the paper’s central claim is “prediction of TS structures” for reactions, the validation must directly test that relationship rather than relying primarily on optimizer behavior.\n“Among the 1196 test molecules, 1122 (93.8%) of the molecular structures are successfully converged. This high success ratio implies that the model inferences provide structures close to the reference ones.”\nThe implication that convergence “implies” proximity to the reference is not logically guaranteed for TS searches, where optimization basins can lead to alternate saddle points or unintended reactions. The paper itself later notes non-uniqueness of reaction paths and that even large energy differences can still be classified as “IRC success,” which further weakens the inference that convergence implies correctness. Moreover, a high convergence rate can reflect that the predicted structure is a decent optimizer starting point, not that the ML prediction is chemically faithful to the intended transformation. Without systematically confirming reactant/product connectivity for converged structures, this statement over-interprets what convergence demonstrates. This affects the reliability of the paper’s headline performance claim.\n“The structures with errors greater than 0.1kcal/mol (shown on the right-hand side of the red line in Fig. 4 (b) ) are selected for testing (126 cases). If the reference reactant and product structures are obtained by IRC calculations, the cases are classified into the IRC success group, otherwise, they are classified into the IRC failure group.”\nThis explicitly shows IRC validation is restricted to a subset selected by a post hoc energy-error threshold, rather than being applied broadly to the test set. Selecting only high-energy-error cases creates a biased sample that cannot support any global statement about what fraction of all converged TSs connect the intended reactants/products. It also leaves open the possibility that many low-energy-error cases still correspond to incorrect reaction pathways (e.g., wrong connectivity but similar energies within the same method). Because the paper uses the overall 93.8% convergence rate and 0.1 kcal/mol threshold as headline claims, the validation should be representative of those populations. Standard practice in TS validation is to use IRC (or equivalent connectivity checks) precisely because energy/convergence are insufficient.\n“Interestingly, this same products are generated by IRC validation of the reference TS structure.”\nThis admission shows that even the reference TS in the dataset can lead, under the authors’ own validation pipeline, to products different from the labeled reference product. That makes the paper’s reliance on “reference” energies and geometries problematic as ground truth for validating chemical correctness. It also raises the possibility that some reported “successes” (convergence or small energy differences) are successes relative to a flawed reference rather than to the intended reaction transformation. In such settings, a robust evaluation would either (i) validate connectivity for a representative portion of the dataset or (ii) redefine success criteria in terms of recovered reactant/product identities rather than energy proximity. As written, the paper’s validation metrics are not robust to the acknowledged reference inconsistencies.\n“It then feeds the optimized transition state to two intrinsic reaction coordinate (IRC) calculations, which link the saddle point to its corresponding reactant and product PES minima by a mass-weighted downhill optimization.” [2](#ref2)\nThis describes a standard, rigorous TS verification workflow used in closely related ML TS-generation work: after TS optimization, run forward and reverse IRC and verify recovered minima. Compared to this practice, the reviewed paper’s selective IRC testing (only 126 cases chosen by energy error) is insufficient to justify global correctness claims. The cited workflow clarifies why convergence to a saddle point is not enough: the key question is whether that saddle point connects the intended minima. In the reviewed paper, this connection is only partially tested, and therefore the reported global success ratios are overstated. Aligning with community practice would require applying IRC/connectivity checks to a much larger and representative portion of the test set.\n“Following the intrinsic reaction coordinate (IRC) implies following the steepest descent path from the transition state to reactants and products.” [5](#ref5)\nThis definition underscores why IRC is central when claiming a TS corresponds to a specific reaction: it explicitly traces the path from the TS to reactant and product basins. The reviewed paper’s headline metrics (convergence and energy differences) do not provide this pathway information. Consequently, without broad IRC-based validation (or an equivalent connectivity verification), the paper cannot reliably claim that predicted TS structures correspond to the intended transformations across the dataset. The paper’s own example where the reference TS yields an unexpected product further motivates the need for path-based validation rather than energy-only metrics. This gap directly impacts validity because TS correctness is fundamentally a pathway/connectivity question.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|GPT|2", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "This paper makes an overgeneralized methodological claim (Validity, Conclusions) that the approach “can be extended to all types of chemical reactions” and “any type of element,” but the demonstrated training/validation domain is limited to small organic reactions and a narrow element set, so the stated scope is not supported by the evidence presented.\n\n“To achieve high accuracy with the satisfaction of various necessary invariances, the ML model contained PSI layers designed to handle any size of molecules and any type of element. This layer relies not on any prior knowledge of chemical reaction type but on reactant and product structures, thus can be extended to all types of chemical reactions without modifications.”\nThis passage is a strong claim about universality across both molecular size and element types, extending beyond the experiments reported in the paper. Demonstrating size-extensivity or permutation invariance does not by itself demonstrate accuracy across arbitrarily large molecules, transition-metal chemistry, charged states, or elements not present in training. In chemical ML, “can be extended” typically requires either training on representative chemistry or explicit experiments showing transfer to new element sets or reaction classes. The paper does not provide such out-of-domain experiments or ablations demonstrating that embeddings/generalization remain reliable when introducing unseen elements. Therefore, the claim is not supported by the presented empirical evidence and risks misleading readers about the method’s validated scope.\n“In this study, two publicly available reaction databases are used. The first was released by Grambow et al.[28] … ωB97X-D3/def2-TZVP results (11961 reactions) … The second database includes 53 S_N2 reactions …”\nThis sentence defines the effective experimental domain of the work: a single large dataset derived from a specific automated reaction-discovery pipeline and a very small SN2 set. These two datasets do not span “all types of chemical reactions” in the usual sense (e.g., multi-step mechanisms, organometallic catalysis, ionic and solvent-mediated reactions, excited states, etc.). The small SN2 dataset also limits the strength of any claims about generalization across reaction mechanisms. Because the paper ties broad scope to model design rather than to demonstrated transfer, the empirical support is not commensurate with the breadth of the claim. A more accurate conclusion would restrict the claim to the element/reaction types present in these datasets.\n“we used automated potential energy surface exploration to generate 12,000 organic reactions involving H, C, N, and O atoms calculated at the ωB97X-D3/def2-TZVP quantum chemistry level.” [1](#ref1)\nThis establishes that the primary dataset used by the reviewed paper is restricted to a limited element set (H/C/N/O) and a specific computational level of theory. If the training data do not include other common elements in organic chemistry (e.g., halogens, sulfur, phosphorus) or any transition metals, the paper’s claim of “any type of element” cannot be empirically supported by the reported experiments. Generalization to unseen elements is nontrivial because learned embeddings and distance distributions can shift substantially when element types change. Therefore, the broad applicability claim conflicts with the scope of the dataset used for training and testing. At minimum, the paper would need separate evaluation on datasets with broader element coverage to justify such statements.\n“Because of the unfavorable scaling of quantum chemical calculations, we only considered molecules with at most seven heavy atoms (C, N, O).” [1](#ref1)\nThis dataset design choice sharply constrains molecular size and composition, which is directly relevant to the reviewed paper’s “any size of molecules” claim. Even if the model architecture is formally size-extensive, accuracy and stability of predictions can degrade with increasing size due to long-range distance distributions, conformational complexity, and combinatorial growth in pairwise interactions. Without evaluation on larger molecules, it is not justified to claim practical applicability to “any size” TS structures. This mismatch between stated scope and demonstrated domain affects how readers should interpret the significance and usability of the method. It also suggests that additional experiments are needed before making general claims about scaling.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|GPT|3", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "The paper’s experimental reporting (Data and methodology) is insufficient for independent reproduction because the implementation and key hyperparameters are delegated to an unversioned external repository and supplementary material not contained in the main paper package, and the provided code artifacts do not include the described TS-prediction model or scripts.\n\n“The implemented model and scripts for training and inference are uploaded at https://gitlab.com/sunghwan.choi/learnts. All hyperparameters used to train the model are summarized in Table S1.”\nThis statement places the essential implementation details and hyperparameters outside the main manuscript. For reproducibility, readers typically need an archived, versioned snapshot (commit hash, release tag, or DOI) and a complete configuration that reproduces reported results. A bare URL without a version identifier does not guarantee long-term accessibility or that the referenced code corresponds to the paper version. Additionally, “Table S1” is required to know model configuration, but it is not included in the main text and, in the provided materials, is not available as a readable supplementary table. As a result, the methodology as packaged is not sufficient for an independent group to reproduce the training or inference pipeline.\n“Supplementary Files\n\nThis is a list of supplementary files associated with this preprint. Click to download.\n\n• v2Supportinginformation.docx”\nThe paper explicitly depends on supplementary material for crucial training details (e.g., hyperparameters in Table S1), but the supplementary content is not integrated into the main preprint. In practice, missing or inaccessible supplementary files prevent verification of architecture, feature settings (e.g., Gaussian grid), loss weights, and training schedules—parameters that can materially affect outcomes in deep learning. Because the paper reports substantial performance improvements over prior models, the lack of a self-contained description makes it difficult to assess whether the comparison is fair and whether the results are robust. This is a significant reproducibility deficiency rather than a cosmetic documentation issue. Standard reproducibility expectations in ML-enabled chemistry papers include providing a complete experimental configuration and scripts to run the pipeline.\n```markdown\n**The deep learning framework to pretrain and finetune AI models.**\n\n**Serving models?** Use [LitServe](https://github.com/Lightning-AI/litserve?utm_source=ptl_readme&utm_medium=referral&utm_campaign=ptl_readme) to build custom inference servers in pure Python.\n```\nThis excerpt from the provided codebase indicates that the code artifact is the general PyTorch Lightning framework rather than the paper-specific TS prediction implementation (PSI layers, distance prediction, NLOpt reconstruction, TTA/ensemble logic, etc.). A reader cannot reproduce the reported experiments from a generic training framework alone; the core model definition, data preprocessing, and evaluation scripts are necessary. The mismatch between what is described (a bespoke PSI-based model for TS distance prediction) and what is provided (a general deep-learning framework) prevents replication and auditing of key choices. This is a major issue because the paper’s claims depend on nuanced methodological details (e.g., distance-matrix constraints, ensemble/NLOpt procedures). Without the actual implementation, reproducibility and detailed methodological scrutiny are not possible.\n“With the exception of the growing string method code … and the Q-Chem quantum chemistry package, all code necessary to reproduce the generated data is available on GitHub …” [1](#ref1)\nThis illustrates a reproducibility standard for the underlying dataset used in the paper: the dataset authors provide a public, script-based pipeline describing how the data were generated. In contrast, the reviewed paper’s model-training pipeline is not similarly reproducible from the materials provided because its core code/hyperparameters are not available in an archived and directly runnable form. Given that the paper’s contribution is primarily methodological (a new TS structure predictor), its own training/inference code should meet at least the same standard of accessibility and specificity. Otherwise, independent verification cannot distinguish genuine methodological improvement from implementation-dependent effects. This comparison highlights why delegating critical information to non-archived supplementary sources is insufficient.\n“Our code is available on GitHub at https://github.com/PattanaikL/ts_gen.” [2](#ref2)\nThis provides an example from a closely related TS-generation ML paper of how the community enables reproducibility: an explicit public code repository is given in the paper itself. The reviewed paper instead relies on an external GitLab URL without version pinning and, in the provided package, does not include the described model code. Because model performance can be sensitive to preprocessing details, training hyperparameters, and optimization procedures, having runnable code is crucial to validate and extend the work. The lack of readily accessible and complete code materially limits the scientific value of reported benchmarks and prevents straightforward follow-up studies. This is particularly important because the paper claims strong performance gains over TSGen and TSNet.", "reviewer_type": "ai", "label": "error", "error_type": "Neglect", "label_origin": "expert+llm-filter"}
{"id": "prb|4|GPT|4", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "The experimental design (Conclusions; Data and methodology) relies on a random 80/10/10 split, which is widely recognized to be an optimistic evaluation for chemical ML and does not substantiate the paper’s broad claims about generalization across reaction space.\n\n“The database, is split randomly into training, validation, and test sets with an 80-10-10 ratio.”\nA random split primarily measures interpolation performance under the same chemistry distribution, which can overestimate real-world generalization when near-duplicate molecules or closely related reactions appear across splits. For reaction and molecular datasets, more challenging splits are often used to approximate prospective generalization, such as scaffold splits or splits by reaction templates/mechanistic families. Because the paper’s narrative emphasizes “general” reactions and broad applicability, the evaluation should stress out-of-distribution settings rather than a single random split. The paper does not report sensitivity to alternative splits or any analysis of similarity between train and test reactions. This limits the strength of the conclusions drawn from the benchmark.\n“Here, a novel ML model that infers TS structures of general single-step reactions is proposed …”\nThe claim of covering “general single-step reactions” implies the model can generalize beyond narrow subsets of chemistry. However, the reported evaluation setup (random split) does not directly test such generalization and therefore cannot fully support this framing. In chemical ML, “general” typically implies robustness to new scaffolds, new functional group combinations, or new reaction templates not seen during training. Without explicit out-of-distribution testing, readers cannot assess how performance degrades as test reactions become less similar to training reactions. Thus, the evaluation protocol does not match the breadth of the conclusion.\n“Random splitting, common in machine learning, is often not correct for chemical data.” [4](#ref4)\nThis statement from a widely used molecular ML benchmark highlights that random splits can be misleading in chemistry due to structured chemical similarity and non-i.i.d. sampling. The reviewed paper’s sole reliance on a random split is therefore at odds with established best practices for evaluating chemical ML generalization. Given the paper’s claims of broad applicability, it is particularly important to avoid overly optimistic splits that might inflate apparent performance. The cited source does not imply random splits are always invalid, but it clearly motivates complementary split strategies to assess robustness. The reviewed paper does not provide such complementary evaluations.\n“Since scaffold splitting attempts to separate structurally different molecules into different subsets, it offers a greater challenge for learning algorithms than the random split.” [4](#ref4)\nThis clarifies a concrete, commonly used alternative evaluation strategy that better probes generalization by separating chemical cores. For TS structure prediction, analogous strategies (e.g., splitting by reactant scaffold or reaction template) would more directly test whether the model generalizes to new chemistry rather than memorizing patterns in similar compounds. The reviewed paper does not report any such robustness checks, yet draws broad conclusions about general reactions. Without these evaluations, it is unclear whether reported improvements would persist in a prospective setting where target reactions differ substantially from those in training. This gap primarily affects the robustness of the paper’s conclusions.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|GPT|5", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "The proposed representation and reconstruction pipeline (Validity; Data and methodology) predicts only interatomic distances and reconstructs coordinates via nonlinear optimization, which is inherently ambiguous up to reflection and therefore cannot, in general, distinguish enantiomeric or mirror-related TS geometries; this undermines claims of general 3D TS structure prediction.\n\n“The model is designed to predict the interatomic distances of TS structures … The model outputs are then converted to the predicted interatomic distances (\\( d^{TS}_{ij} \\)) and used to generate the atomic positions in the TS structures (\\( X^* \\)) by nonlinear optimization.”\nThis describes a pipeline where the predicted object is a distance matrix, not a unique 3D geometry, and the final coordinates are obtained by a reconstruction step. Distance matrices determine structures only up to rigid motions and reflection, so the reconstruction can yield mirror images that are indistinguishable in distance space. For many applications, especially stereoselective chemistry, mirror-related TS structures are not interchangeable because they can correspond to different stereochemical outcomes or interact differently with chiral environments. The paper does not discuss or evaluate this ambiguity, yet presents the method as predicting “TS structures” in a general sense. This methodological limitation affects the validity of broad structural claims.\n“The pair features satisfy the translational and rotational invariances because neither atomic numbers nor distances are changed by translation or rotation.”\nWhile translational and rotational invariance are desirable, the features described here are also invariant to reflection because distances are unchanged under mirror operations. That means the model input and output spaces cannot encode chirality or handedness information required to distinguish enantiomeric configurations. The paper does not provide an additional mechanism (e.g., signed volumes or chiral constraints) to break this symmetry in reconstruction. As a result, the method can be fundamentally unable to represent certain stereochemical distinctions even before considering model error. This is not a minor detail because TS stereochemistry can be central in organic reaction outcomes.\n“First, we directly output Cartesians as opposed to distance matrices. … it affords our model the ability to differentiate enantiomers – something not possible with only a distance matrix.” [3](#ref3)\nThis explicitly states, in a closely related TS structure prediction paper, that distance-matrix approaches cannot distinguish enantiomers, motivating direct Cartesian (equivariant) prediction. The reviewed paper’s method is distance-matrix-based and therefore inherits this limitation unless it introduces extra orientation/chirality constraints, which it does not. This directly conflicts with broad claims of predicting general TS “structures,” because in the presence of chirality the structure is not uniquely defined by distances alone. Even if some datasets do not emphasize enantioselective reactions, the paper’s own scope statements are general enough that this limitation should be addressed. The absence of such discussion or experiments weakens the methodological completeness.\n“Because we use the distance matrix to generate a TS structure, the target geometry is not entirely unique, and in a few cases, this fact results in a converged TS guess that contains one or more planes of symmetry with the ground truth geometry.” [2](#ref2)\nThis is a direct acknowledgment, from a distance-matrix TS-generation approach, that non-uniqueness can manifest as mirror-related structures and can affect downstream optimization/verification. The reviewed paper similarly reconstructs coordinates from predicted distances, but it does not report whether such mirror ambiguities occur or how often they lead to failed or incorrect TS optimizations. Without quantifying or mitigating this issue, the method’s reliability for general TS prediction remains uncertain, particularly for cases where mirror symmetry is chemically consequential. The cited evidence shows this is not a hypothetical corner case but a known issue in the immediate literature. Therefore, the reviewed paper should either constrain chirality/orientation or explicitly scope its claims.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "The use of a random split for the dataset likely leads to data leakage, overestimating the model's generalization capability, as the dataset contains chemically similar reactions generated by automated exploration.\n\n\"The database, is split randomly into training, validation, and test sets with an 80-10-10 ratio.\"\nThe paper explicitly states that a random split was used. In chemical datasets, random splitting is known to be problematic because it places structurally similar molecules or reactions (e.g., conformers or analogs) in both the training and test sets.\n\"The first was released by Grambow et al.[28]... 11961 reactions are employed\"\nThe Grambow et al. dataset (ReactionData) consists of elementary reactions generated by automated exploration algorithms (like GSM). These algorithms often generate clusters of very similar reactions (e.g., the same reaction template applied to slightly different substrates).\n\"Reactants, products, and transition states of elementary chemical reactions based on quantum chemistry\" [1]\nThe nature of the dataset implies high redundancy. By using a random split, the model can achieve high accuracy by memorizing the local manifold of reaction types seen during training, rather than learning generalizable chemical rules. A scaffold split or reaction-type split is required to properly evaluate the model's ability to generalize to new reactions.\n\nReferences:\n[1] Grambow, C.A., Pattanaik, L., Green, W.H.: Reactants, products, and transition states of elementary chemical reactions based on quantum chemistry. Scientific Data 7(1), 1–8 (2020). https://doi.org/10.1038/s41597-020-0460-4", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "The model predicts the ratio of TS distance to interpolated distance, which is numerically unstable and prone to exploding values when the interpolated distance is small.\n\n\"the model predicts the normalized distances of TS structures by those of the interpolated structure (\\( d^{TS}_{ij}/d^{l}_{ij} \\)).\"\nThe target variable is defined as the ratio of the transition state distance to the linearly interpolated distance. This formulation is risky because if the denominator \\( d^{l}_{ij} \\) approaches zero, the ratio explodes.\n\"Linear interpolated geometries are frequently used for TS search algorithms because of their reliable structures and low costs. [13, 37]\"\nThe paper cites linear interpolation (LST) as a standard method. However, LST in Cartesian coordinates (which is implied by \"linearly interpolated structures\") often results in unphysical geometries where atoms can overlap or pass through each other, leading to near-zero interatomic distances (\\( d^{l}_{ij} \\approx 0 \\)). The paper does not describe any mechanism to handle these singularities (e.g., clipping, log-space prediction), which casts doubt on the robustness of the method.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "The loss function designed to enforce Euclidean constraints is mathematically insufficient as it only constrains the rank and trace of the distance matrix, failing to ensure the positive semi-definiteness required for a valid Euclidean Distance Matrix (EDM).\n\n\"The 3D Euclidean distance matrices can have at most 5 nonzero eigenvalues and the the sum of eigenvalues should be zero.[40]\"\nThe paper correctly identifies that a distance matrix for points in 3D has a rank of at most 5 and a trace of 0. However, these are necessary but not sufficient conditions.\n\"\\( L_3 = \\sum_{i=1}^{\\min(5,N_{\\text{atom}})} e_i + \\sum_{i=\\min(5,N_{\\text{atom}})}^{N_{\\text{atom}}} |e_i| \\)\"\nThe proposed loss function \\( L_3 \\) minimizes the magnitude of eigenvalues beyond the 5th one and enforces the sum of the first 5 to be zero (implied by trace=0). However, a valid EDM must also satisfy specific inertia properties (e.g., having exactly one positive eigenvalue for the distance matrix itself, as discussed in Gower [4]). The proposed loss allows for invalid matrices (e.g., with incorrect eigenvalue signs) that satisfy the rank/trace conditions but cannot be embedded in 3D Euclidean space.\n\nReferences:\n[4] Gower, J.C.: Properties of Euclidean and non-Euclidean distance matrices. Linear Algebra and its Applications 67, 81–97 (1985). https://doi.org/10.1016/0024-3795(85)90187-9", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Gemini|5", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "The provided code archive contains the source code for the PyTorch Lightning library instead of the implementation of the proposed model, making it impossible to reproduce the results or verify the implementation details.\n\n\"The implemented model and scripts for training and inference are uploaded at https://gitlab.com/sunghwan.choi/learnts.\"\nThe paper claims the code is available. However, the code provided for review (in the `code` directory) does not contain the \"learnts\" project.\n\"# Why PyTorch Lightning? Training models in plain PyTorch requires writing and maintaining a lot of repetitive engineering code.\"\nThe `README.md` file in the provided `code` directory identifies the content as the PyTorch Lightning library itself.\n\"name='lightning', version=__version__,\"\nThe `setup.py` file in the provided `code` directory confirms that the package being installed is `lightning`, `pytorch_lightning`, and `lightning_fabric`. There is no source code for the proposed TS prediction model, preventing any form of reproducibility or code verification.", "reviewer_type": "ai", "label": "error", "error_type": "Neglect", "label_origin": "expert+llm-filter"}
{"id": "prb|4|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "This work exploits extensive reaction dataset of Grambow et al. which contains 10k reactions with atomic indices already mapped between reactant and product. If I understood correctly, in Pair sequence interface layer process, permutation-invariance and size-extensivity are preserved in transformer encoder but it seems correct atom mapping of reactant and product seem to be assumed in “Bidirectional GRU” step. However in other many cases, outside of this dataset, this correct atom mapping between reactant and product is not guaranteed to exist and itself is not a trivial problem. Although this model exhibits excellent performance within current dataset as training input, the author may need to address its applicability toward general molecular reactions. Please clarify in the manuscript if this model can be also generally applicable to any elementary reaction or it requires the atom-mapping process as preliminary step.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "As this is being machine learning approach, its performance/accuracy scales with the size of the training set. Although dataset of Grambow et al. has vast number of reactions, real applications always involve building up their own reaction data and this is even more stipulated by the failure case given in this manuscript. In this work training-validation-test set as splited into 8-1-1 ratio, but would be interesting to present performance improvement with respect to number of training set (learning curve). Then readers might be able to expect approximated accuracy when trained with this model.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "Fig 2. should be improved with better visualization. Font is too small and color should be more differentiable.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "It’s hard to follow what actually “test-time augmentation (TTA)” means in current manuscript without reading the references cited. The author might want to elaborate further in the manuscript regarding this part.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "In Fig. 4. There are success after/before optimization. If author meant success as convergence of saddle-point optimization, how can you confirm its success even before optimization? Also success is ambiguous terminology which can be better expressed with “converged”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "In page 10, “challenging but demanding work” is awkward expression.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "Regarding saddle-point optimization, author should clarify which specific algorithm has been used in Qchem and which convergence criteria has been imposed in this work. (e.g. Minimum force)", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Human_1|9", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "Author indicates rotational and translation entropy have been used to encode reaction property, but its notations are wrong. I.e. S_vib and S_rot, which are vibrational and rotational entropy. Also author needs elaboration why only two components of entropy are used instead of three (e.g. vibrational, rotational and translational entropy)", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Human_1|10", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "There are several typos throughout the manuscript and these have to be revised before publication.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "It is unclear to me how the author plans to handle chirality with their proposed model. As they state (in many places) most clearly on page 16, \\\"... the ML model predicts only interatomic distances\\\". It is, of course, an inconvenient truth that a stereogenic carbon with 4 unique substituents will produce an equivalent distance matrix of all enantiomers. I cannot interpret how the authors subsequent non-linear optimization step would correct this oversight. So, I ask the author to address this. Specifically, can the model succeed in stereochemical TS predictions? And if so, how?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "Unfortunately the grammar of the manuscript needs a lot of work. I trust that the Springer/Nature editorial team can work with the author to revise. I spotted no less than 20 errors.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "I was particularly impressed with the authors ensemble approach, which endows the model with the ability to find multiple TS structures between a particular pair of RC and PC. This is a particularly clever solution to the problem of PES complexity.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "I found it peculiar that exactly 1196 \\\"test molecules\\\" were selected from the Grambow database for further analysis by optimization (page 8). However, the database contains 11961 reactions (page 13). Is this just a strange coincidence or a typo? If only a coincidence, can the author clarify how the 1196 test molecules were selected from the larger 11961 set?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "Again, I was confused about the statement on page 9 regarding the error in absolute energy of the optimized structures. It isn't clear to me how one measures this error. I understand that a TS is predicted from the ML model and that is a \\\"predicted\\\" structure. Subsequently a user can optimize that predicted structure using a traditional saddle point optimization from first principles. Therefore an \\\"error\\\" can be determined from the difference in energies of these two structures. However, What structure does one compare to if they wish to assess the error of the \\\"optimized\\\" TS structure? Even the reference database used the same theoretical technique (namely, ωB97X-D3/def2-TZVP). I would ask that the author please elaborate on their explanation of \\\"error\\\" for optimized structures.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "I am not particularly in favour of the authors TTA approach. In this approach, the authors use both the forward and reverse directions of a reaction to essentially generate \\\"more\\\" data in a somewhat artificial way. The result may be that the prediction becomes directionally invariant but I believe there is a significant risk of overfitting in doing so. My preference would be for directional invariance to be \\\"baked in\\\" to the model. I am not, however, asking the author to develop a new model but I would demand to see more training statistics. A training curve is an important element of any ML paper that is sorely lacking in this work.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "Kinetic modeling is a visual science, but the reader sees very few examples of the model’s predictions. I recommend an additional figure, either in the main text or the supplement, showing examples of the model’s predictions--both good and poor. Including both unimolecular and bimolecular reactions would be nice. This will help the reader gain confidence in the model’s ability and may highlight areas for improvement.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "I especially like the modeling choice to predict a multiplier to the ratio of the interpolated distance matrix and the TS distance matrix. Did you test predicting the distance value directly? I’m curious to know if this makes a substantial difference (not a necessary experiment).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "I’m not sure that TTA is worth highlighting, since according to Fig. 2, it does not improve model performance much.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "I appreciate the information Fig. 3b is trying to convey, but it’s difficult to read, especially with all the different colored histograms in the background. At the very least, I suggest making this figure much larger, but I would try to improve its readability.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "While it is nice that ~94% of the optimizations converged, one should perform frequency calculations and verify the presence of exactly one imaginary frequency to correctly characterize the saddle point. I highly recommend that this analysis be performed for all of the successful optimizations. They should definitely be performed for the 126 cases with energies differences higher than 0.1 kcal/mol. Without a proper frequency analysis, it is uncertain whether the structures are true TS structures (even if they were verified by IRC).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "There are few key limitations the author should highlight. First, that the reactant and product geometries used to generate TS guesses in this study were obtained from the Grambow dataset and are hence QM-optimized reactants and products. Thus, the model still requires QM-optimized reactants and products as input, which should be clearly stated in the manuscript. Second and more importantly, for any bimolecular reactions, the reactants and products need to be aligned in a reacting configuration, which is inherently the case in the Grambow dataset because the data were generated using the growing string method. A typical workflow performs opt-freq calculations on each species independently as traditional TST calculations expect partitions functions for each species rather than for the VDW complex that is found in the Grambow dataset. For reactions that have 2 or 3 products, which represent about 30% of this dataset, it would normally require another step to align these species to create the complex that was used to train the model presented here. Without a robust alignment scheme, it is unclear whether or not the presented model can be successfully applied to bimolecular reactions. This limitation should also be clearly stated in the paper.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Human_3|7", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "To train the TS model, Choi uses random splits on the Grambow dataset. However, several recent publications have noted the issues with using random splits on this dataset (see ref. 1 and 2). While the dataset contains ~12k unique reactions, it only contains ~1-2k unique reactants. So, when using a random split, some of the reactants may be duplicated in the test set. For TS geometry prediction, this is not a severe issue, but I suggest reproducing Fig. 2 using reactant-based scaffold splits (see ref. 2 for additional details). There’s no need to redo the QM optimization section. [1].Heid, E., & Green, W. H. (2021). Machine learning of reaction properties via learned representations of the condensed graph of reaction. Journal of chemical information and modeling. [2].Spiekermann, Kevin A., Lagnajit Pattanaik, and William H. Green. \\\"Fast Predictions of Reaction Barrier Heights: Toward Coupled-Cluster Accuracy.\\\" The Journal of Physical Chemistry A 126.25 (2022): 3976-3986.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Human_3|8", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "I didn’t quite understand the model loss functions for the reactant and product readout layers. These layers are predicting the energy and entropy of the reactants and products? This description (pg. 14) could be clarified. Further, while I understand the motivation for these readout layers (i.e. benefits of multitask training), it is not demonstrated whether this strategy is actually useful. Experiments ablating these readout layers would be helpful.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Human_3|9", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "The statement at the beginning of section 4.5 is not exactly true. First, the model from ref. 3 does in fact predict an interatomic distance matrix, but it reconstructs Cartesian coordinates from the predicted distance matrix in an end-to-end fashion. So the statement that “previous studies...directly infer the 3D atomic positions” isn’t strictly true. In fact, the nonlinear optimization used here is nearly identical to the one used in ref. 3, aside from the fact that ref. 3 used learned weights (w_ij). Second, an important work which was missed in the citations (ref. 4), uses a related approach of predicting a Columb matrix intermediate and obtaining the Cartesian coordinates through an optimization. [3].Pattanaik, L., Ingraham, J. B., Grambow, C. A., & Green, W. H. (2020). Generating transition states of isomerization reactions with deep learning. Physical Chemistry Chemical Physics, 22(41), 23618-23626. [4].Makoś, M. Z., Verma, N., Larson, E. C., Freindorf, M., & Kraka, E. (2021). Generative adversarial networks for transition state geometry prediction. The Journal of Chemical Physics, 155(2), 024116.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|4|Human_3|10", "source": "prb", "split": "test", "paper_id": "prb4", "comment": "The choice of 90 models for the ensemble seems a bit excessive and may negatively impact downstream usage (i.e. longer runtimes). It would be nice to include some analysis on how many models are truly necessary as the choice of 90 seems arbitrary.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|5|Claude|1", "source": "prb", "split": "test", "paper_id": "prb5", "comment": "The paper presents all benchmark results (Tables I-VI) as single point estimates without any error bars, standard deviations, or confidence intervals from multiple training runs, making it impossible to assess the statistical significance of the claimed performance improvements over competing methods.\n\n\"TABLE I: MAE of force components on the MD-17 data set, trained on 1,000 configurations, forces in units of [meV/Å]. For the benzene molecule, two different data set exists from [17, 31] with different levels of accuracy in the DFT reference data.\"\nThis table presents single MAE values for NequIP and comparison methods (SchNet, DimeNet, sGDML, FCHL19/GPR) without any uncertainty measures. Given that neural network training involves stochastic elements such as random weight initialization, data shuffling, and potentially different train/validation splits, the actual performance can vary significantly between runs. Without error bars from multiple independent training runs with different random seeds, it is impossible to determine whether the reported differences between methods (e.g., NequIP's 11.2 vs FCHL19/GPR's 11.2 meV/Å for Malonaldehyde) are statistically significant or within natural variance.\n\"We train a series of networks with identical hyperparameters, but vary the training set sizes between 10 and 1,000 structures, sampled uniformly from the full data set, as well as a validation set consisting of 100 structures.\"\nEven for the ablation study in Figure 7 comparing l=0 vs l=0/l=1 networks, the paper does not report error bars despite the learning curves being critical evidence for the claimed data efficiency advantage of equivariant features. The figure shows smooth curves without any indication of variance across runs, which is inconsistent with typical neural network training behavior where different random seeds can lead to noticeable performance variations.\n\"We measure the Li diffusivity in ten Nequip-driven MD simulations (computed via the slope of the mean square displacement), all of length 50 ps and started from different initial velocities, randomly sampled from a Maxwell-Boltzmann distribution. We find a mean diffusivity of 1.42 × 10⁻⁵ cm²/s\"\nWhile the paper runs ten MD simulations for diffusivity measurements, it only reports the mean value without the standard deviation across these ten runs. This is a missed opportunity to demonstrate statistical reproducibility. Additionally, this approach of running multiple simulations is not applied to the model training itself—no information is provided about variance in model performance when trained with different random seeds.\n\"For each task, we trained four independent models using different random seeds and report the mean and standard deviation of these independent runs\" [[1]](#citation-list)\nIn contrast to this paper, the published version in Nature Communications includes error bars and multiple training runs, following the best practices established in contemporary machine learning benchmarking. The preprint version under review lacks this critical statistical rigor that is necessary to validate the claimed improvements.\n\nReferences:\n[1] Batzner, S. et al. \"E(3)-equivariant graph neural networks for data-efficient and accurate interatomic potentials.\" [Nature Communications 13, 2453 (2022)](https://doi.org/10.1038/s41467-022-29939-5)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|5|Claude|2", "source": "prb", "split": "test", "paper_id": "prb5", "comment": "The comparison between NequIP (133 training structures) and DeepMD (133,500 training structures) in Table III does not constitute a valid data efficiency comparison because it compares different architectures at vastly different operating points rather than showing learning curves for both methods.\n\n\"A DeepMD NN-IP model was previously trained [15] for water and ice using a joint training set containing 133,500 reference calculations of these four systems. To assess data efficiency of the NequIP architecture, we similarly train a model jointly on all four parts of the data set, but using only 133 structures for training, i.e. 1000x fewer data.\"\nWhile this comparison shows that NequIP achieves better force RMSE with 133 structures than DeepMD does with 133,500 structures, it does not actually demonstrate \"data efficiency\" in the proper sense. Data efficiency would require showing that NequIP consistently achieves lower errors than DeepMD at the same training set size, or equivalently, that NequIP reaches a target accuracy with fewer data points. The comparison as presented could simply mean that NequIP is a fundamentally better architecture regardless of data size, rather than being more \"data-efficient.\"\n\"TABLE III: Root mean square error (RMSE) of force components on liquid water and the three ices in units of [meV/Å]. Note that the NequIP model was trained on < 0.1% of the training data of DeepMD.\"\nA proper data efficiency study would train both NequIP and DeepMD on identical training set sizes (e.g., 10, 50, 100, 500, 1000, 10000 structures) and plot learning curves showing error as a function of training data size. This is precisely what the paper does for the l=0 vs l=0/l=1 comparison in Figure 7, but fails to do for the DeepMD comparison. Without this, the 1000x claim is scientifically imprecise because we cannot determine where the crossover point is or whether DeepMD might actually be more data-efficient at certain data regimes.\n\"The algorithm learns as new data become available. Empirical results have shown that this exponent typically remains fixed across different learning algorithms for a given data set, and different methods only shift the learning curve, leaving the log-log slope unaffected\" [[1]](#citation-list)\nThe published Nature Communications version acknowledges that different methods often have similar scaling exponents, meaning they learn at similar rates as data increases. The preprint's comparison at a single point (133 vs 133,500) cannot capture this scaling behavior, which is essential for characterizing data efficiency.\n\nReferences:\n[1] Batzner, S. et al. \"E(3)-equivariant graph neural networks for data-efficient and accurate interatomic potentials.\" [Nature Communications 13, 2453 (2022)](https://doi.org/10.1038/s41467-022-29939-5)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|5|Claude|3", "source": "prb", "split": "test", "paper_id": "prb5", "comment": "The ablation study in Figure 7, which is central to the claim that equivariant features are responsible for data efficiency gains, does not adequately control for differences in model capacity (number of parameters) between the l=0 and l=0/l=1 networks.\n\n\"In particular, we run a set of experiments for a system with a fixed number of training configurations in which we explicitly turn on or off interactions of higher order than l = 0. This defines two settings: first, we train the network with both l = 0 and l = 1 features and all five interactions as previously outlined in this work. Second, when all interactions involving l = 1 are turned off, this turns the network into a conventional invariant GNN-IP, involving only invariant convolutions over scalar features in a SchNet-style fashion.\"\nThe l=0/l=1 network inherently has more parameters than the l=0-only network because it includes vector features and additional tensor product operations. The paper states \"identical hyperparameters\" are used, but this does not account for the fact that the l=0/l=1 network has fundamentally higher capacity. The observed performance difference could be attributed to increased model capacity rather than the specific benefits of equivariant operations. A controlled comparison would either match the total parameter count between architectures or show that increasing the l=0 network's parameters (e.g., more channels, layers) does not close the gap.\n\"We further note, that in [39], a Behler-Parrinello Neural Network (BPNN) was trained on 1303 structures, yielding a RMSE of ≈ 120 meV/Å in forces when evaluated on the remaining 290 structures. We find that NequIP models trained with as little as 50 and 100 data points obtain RMSEs of 122.9 meV/Å and 93.3 meV/Å on their respective test sets\"\nThe comparison with Behler-Parrinello networks is similarly confounded by differences in architecture, hyperparameters, and potentially train/test splits. Without controlling for model size and computational cost, attributing the gains specifically to SE(3)-equivariance is not fully justified.\n\"This suggests that it is indeed the use of tensor (in our specific case vector) features and equivariant convolutions that enables the high data efficiency of NequIP.\"\nThis conclusion, while plausible, is not rigorously supported by the experimental design. The claim would be strengthened by showing that (a) l=0 networks with matched parameter count still underperform, (b) l=0 networks with significantly more parameters cannot match l=0/l=1 performance, or (c) theoretical analysis of the inductive bias provided by equivariance.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|5|Claude|4", "source": "prb", "split": "test", "paper_id": "prb5", "comment": "For the formate decomposition on Cu system—a scientifically important reactive surface chemistry application—the paper provides only force MAE metrics without MD simulation validation, deferring dynamics analysis to future work.\n\n\"TABLE IV: MAE of force components for Formate on Cu system, per-element basis. The training set consists of 2,500 structures, force units are [meV/Å]\"\nTable IV reports per-element force MAE values (e.g., 2.2 meV/Å for Cu, 24.7 meV/Å for C) but provides no validation that these errors translate to physically meaningful MD simulations. For a reactive system involving C-H bond cleavage and the transition between monodentate, bidentate formate, and CO₂+H states, force accuracy alone is insufficient—the model must correctly predict reaction barriers, transition states, and dynamical pathways.\n\"A more detailed analysis of the resulting dynamics will be subject of a separate study.\"\nThis statement acknowledges the limitation but does not mitigate it for the purpose of this paper's claims. The abstract and introduction emphasize that NequIP \"enables high-fidelity molecular dynamics simulations\" and can reproduce \"structural and kinetic properties... with very high fidelity.\" However, this claim is not substantiated for the reactive formate/Cu system, which is arguably one of the more challenging and scientifically relevant test cases presented. The deferral of dynamics analysis to future work is problematic when the paper's core claim is about MD simulation capability.\n\"The decomposition process of formate on Cu involves configurations corresponding to the cleavage of the C-H bond, initial and intermediate states (monodentate, bidentate formate on Cu < 110 >) and final states (H ad-atom with a desorbed CO₂ in the gas phase).\"\nGiven that the dataset explicitly includes reaction intermediates and products, validating that NequIP can correctly simulate the reaction pathway would significantly strengthen the paper's claims. Other systems (Li₄P₂O₇, LiPS) receive extensive MD validation including RDF, ADF, and diffusivity comparisons with AIMD. The asymmetric treatment of the formate/Cu system leaves a significant gap in the validation.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|5|Claude|5", "source": "prb", "split": "test", "paper_id": "prb5", "comment": "The paper does not provide systematic analysis of energy drift, simulation stability over long timescales, or demonstrate that NequIP-driven simulations remain stable for the duration required for practical applications.\n\n\"We run a series of MD simulations with the NequIP potential trained on 2,500 structures in the NVT ensemble at the same temperature as the AIMD simulation for a total simulation time of 50 ps and a time step of 0.25 fs, which we found advantageous for reliability and stability of long simulations.\"\nThe maximum simulation length reported is 50 ps, which may be insufficient to detect energy drift or identify rare unstable configurations that could cause simulation failures. Many practical applications of MD potentials require simulations on nanosecond to microsecond timescales. The phrase \"we found advantageous for reliability and stability\" suggests that some stability issues were encountered, but no quantitative analysis is provided (e.g., energy drift per nanosecond, percentage of simulations that completed successfully).\n\"Recent studies have shown that force error metrics alone can be poor predictors of MD stability\" [[2]](#citation-list)\nContemporary work on machine learning force fields has highlighted the importance of testing stability beyond force accuracy metrics. Issues such as atomic clashes, unphysical bond breaking, and energy drift can occur even when force MAE is low. The paper would benefit from explicit stability testing, such as running extended simulations and reporting the number of steps until failure or measuring total energy conservation in NVE simulations.\n\"Figure 6 shows the mean square displacements of Li for an example run.\"\nPresenting only \"an example run\" rather than aggregate statistics across multiple simulations does not provide sufficient evidence for reproducibility and stability. While the paper mentions running ten MD simulations for diffusivity, the MSD figure shows only one trajectory comparison, leaving questions about the consistency of dynamics across runs and the potential for outlier failures.\n\nReferences:\n[2] Fu, X. et al. \"Forces are not Enough: Benchmark and Critical Evaluation for Machine Learning Force Fields with Molecular Simulations.\" [Transactions on Machine Learning Research (2023)](https://openreview.net/forum?id=A8pqQipwkt)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|5|GPT|1", "source": "prb", "split": "test", "paper_id": "prb5", "comment": "This paper’s headline conclusions about extreme data efficiency and superiority over prior ML interatomic potentials are not robust because key comparisons (notably the “1000× fewer data” DeepMD comparison) are evaluated on highly correlated MD trajectory frames with train/test splits that can leak near-duplicate configurations, undermining the validity of the reported “orders-of-magnitude” gains.\n\n\"NequIP outperforms existing models with up to three orders of magnitude fewer training data, challenging the widely held belief that deep neural networks require massive training sets.\" \nThis is the central, strongest quantitative claim in the abstract and it materially affects the paper’s conclusions about data efficiency. Because it is a comparative statement (“outperforms existing models”), it requires a tightly controlled evaluation protocol that rules out confounders. In MD-generated datasets, adjacent frames can be extremely similar, so “randomly sampled” training frames can have near-neighbors in the test set even if they are formally disjoint. If such leakage occurs, test errors can substantially underestimate true generalization error for deployment (e.g., new thermodynamic conditions or different trajectories). The paper does not establish that its orders-of-magnitude comparisons are robust to these well-known correlation/leakage effects.\n\"To assess data efficiency of the NequIP architecture, we similarly train a model jointly on all four parts of the data set, but using only 133 structures for training, i.e. 1000x fewer data. The 133 structures were sampled uniformly from the full data set available online, consisting of water and ice structures, made up of a total of 140,000 frames, coming from the same MD trajectories that were used in the earlier work [15]. We also use a validation set of 50 frames and report the test accuracy on all remaining structures in the data set. ... We find that with 1000x fewer training data, NequIP significantly outperforms DeepMD on all four parts of the data set.\" \nThe protocol explicitly samples training/validation frames from the same MD trajectories and then evaluates on “all remaining” frames, which is exactly the situation where temporal correlation can make held-out frames very similar to training frames. That similarity can make interpolation look like strong generalization, especially when the test set contains many near-duplicates of training points. The DeepMD numbers are attributed to a model “previously trained [15]”, but the paper does not specify whether DeepMD was evaluated on exactly the same held-out frames and with the same metric definition, leaving comparability unclear. Since the conclusion hinges on a 1000× data reduction, even modest evaluation mismatches or leakage can qualitatively change the interpretation. As written, the evidence does not justify that the reported 1000× advantage reflects a robust, apples-to-apples generalization improvement.\n\"However, if the data has many similar conditions, e.g., as occurs for data generated from AIMD trajectories or small perturbations to existing structures, then these random CV approaches will yield overly optimistic predictions. The predictions will be overly optimistic due to the “twin” problem, where extremely similar data is present in both the train and test sets, and the model predictions are thus indicative of data that looks just like the training data.\" ([1](#citation-list))\nThis directly describes the failure mode of using random splits on trajectory data: even without explicit leakage, near-duplicate configurations across train/test can yield overly optimistic errors. The paper’s water/ice comparison and several other experiments explicitly sample “uniformly” from MD frames and evaluate on the remaining frames from the same trajectories, matching the scenario warned about here. Because the paper’s main scientific claim is exceptional data efficiency, any optimism bias in the evaluation can inflate the apparent sample-efficiency advantage. The quoted guidance also clarifies what more robust alternatives look like (e.g., testing on new conditions or later trajectory segments), which the paper does not consistently implement for its headline “orders-of-magnitude” comparisons. Therefore, this literature evidence supports that the reported gains may not reflect robust out-of-sample performance.\n\"We show that the proposed scheme provides an efficient and accurate protocol in a variety of systems, including bulk materials and molecules. In all these cases, DPMD gives results that are essentially indistinguishable from the original data, at a cost that scales linearly with system size.\" ([4](#citation-list))\nThis highlights that DeepMD (the principal baseline used for the 1000× claim) is itself presented in the literature as an accurate, symmetry-preserving approach trained on ab initio labels. That makes the paper’s claim of “significantly outperforms DeepMD” with 1000× less data unusually strong, and therefore it warrants especially careful, transparent, and matched evaluation. When a baseline is described as reproducing “results ... essentially indistinguishable from the original data,” modest differences in dataset composition, splitting, and metric definitions can dominate apparent gaps. The paper does not provide enough detail to verify that the DeepMD and NequIP results were produced under identical test conditions. As a result, the conclusion that NequIP fundamentally changes the data requirement relative to DeepMD is not convincingly supported.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|5|GPT|4", "source": "prb", "split": "test", "paper_id": "prb5", "comment": "This paper’s methodological conclusion that the performance/data-efficiency gains are directly caused by the SE(3)-equivariant convolution architecture is not convincingly established, because the presented ablation is limited in scope and does not robustly isolate equivariance from other confounded factors (e.g., representation capacity, split variance, and evaluation difficulty).\n\n\"We directly verify that the performance gains are connected with the unique SE(3)-equivariant convolution architecture of the new NequIP model.\" \nThis is a causal attribution claim, not merely a descriptive performance report, and therefore requires especially careful experimental controls. In ML architecture studies, isolating a causal factor typically involves multiple controlled ablations, matched capacity, and repeated runs across splits/seeds to quantify variance. The paper later provides a specific ablation, but it is limited to a single test system and a single form of “turning off” vector interactions. Without stronger controls, the statement “directly verify” overstates what is actually demonstrated. Because the paper’s broader significance rests on equivariance being the key mechanism, this unsupported causal leap materially weakens the conclusions.\n\"In order to gain insight into the reasons behind increased accuracy and data efficiency, we perform a series of experiments with the goal of isolating the effect of using equivariant convolutions of geometric tensors compared to invariant convolutions over scalars. ... Second, when all interactions involving \\( l = 1 \\) are turned off, this turns the network into a conventional invariant GNN-IP, involving only invariant convolutions over scalar features in a SchNet-style fashion.\" \nTurning off all \\(l=1\\) interactions changes not only equivariance properties but also the representational form and information flow (e.g., removing vector channels and associated tensor products). Even if hyperparameters are “identical,” the effective model class and expressivity can change substantially, so attributing all differences to equivariance alone is not cleanly justified. Additionally, labeling the ablated model as “SchNet-style” does not guarantee equivalence to SchNet’s exact architecture, optimization, and inductive biases, which makes interpretation ambiguous. Since the paper claims to have “isolated” the effect, it should demonstrate that other factors (capacity, parameter count, training stability, and evaluation variance) are controlled or measured. Without that, the ablation supports “equivariant performs better than this particular non-equivariant variant” but not the stronger causal claim.\n\"Finally, we introduce a more challenging benchmark with chemical and structural variations that suggests the path for further work.\" ([5](#citation-list))\nThis highlights that, even within closely related molecular ML potential literature, the community recognizes the need for benchmarks that stress generalization beyond standard MD trajectory interpolation. The reviewed paper’s equivariance ablation is performed on a single bulk-water dataset with random sampling from a finite set of configurations, which may not reflect these harder generalization regimes. If the benchmark is not challenging enough (e.g., due to “twin” configurations or near-interpolation), architectural differences can be amplified or suppressed in ways that do not transfer to harder settings. Therefore, using only such an evaluation to claim a mechanistic explanation for broad data-efficiency gains is insufficient. The cited sentence supports the expectation that stronger, more varied benchmarks are needed before making sweeping causal conclusions about architectural choices.\n\"Averaging an error metric over all *k* folds yields a measure that is less affected by random noise induced by the exact choice of train-/test-set splitting.\" ([2](#citation-list))\nThe reviewed paper’s architectural attribution relies on experiments that use randomly sampled training sets from correlated MD data, but it does not report repeated trials over multiple splits/seeds for the ablation. Without quantifying split-induced variance, it is difficult to know whether the observed gap is stable or partly an artifact of a favorable/unfavorable sampling. The cited sentence articulates why multi-split evaluation (e.g., k-fold or repeated splits) is important to reduce sensitivity to one particular split. Since the paper’s claim is about the *reason* behind data efficiency, it is not enough to show a single curve; it must show robustness across splits. This gap weakens the strength of the mechanistic conclusion.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|5|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb5", "comment": "The paper claims \"favorable computational efficiency\" but fails to provide a computational cost comparison (inference or training time) against other Machine Learning Interatomic Potentials (ML-IPs) such as SchNet, DimeNet, or DeepMD.\n\n\"retaining favorable computational efficiency [1][13].\" (Abstract)\nThe abstract claims that the method retains favorable computational efficiency, implying it is competitive with or superior to existing ML-IP methods. However, this claim is not substantiated with relevant benchmarks against these methods.\n\"Computational Efficiency ... we report the computational efficiency of NequIP and compare it to that of the ab-initio methods on two examples shown in this work: for a molecular system, we choose the Toluene molecule, computed at the CCSD(T)-level of theory [31]; for a material with periodic boundary conditions, we choose the Formate on Cu system, in which reference data were obtained with DFT.\" (Computational Efficiency section)\nThe \"Computational Efficiency\" section only compares NequIP's inference time with *ab-initio* methods (CCSD(T) and DFT). While NequIP is naturally faster than *ab-initio* calculations, the relevant comparison for an ML-IP is against other ML models. Equivariant Graph Neural Networks (GNNs) involving tensor products are typically more computationally expensive than invariant GNNs like SchNet [1] or DeepMD [2]. The lack of comparison with these baselines hides the potential computational overhead of the proposed method.\n\"It should be noted, however, that the evaluation cost of kernel methods scales linearly with the number of training configurations.\" (Introduction)\nThe authors criticize kernel methods for their scaling behavior but do not provide a similar analysis or benchmark for their own method's scaling relative to other neural networks. Later work by the same authors (Allegro [3]) explicitly addresses the scalability limitations of NequIP, noting that its message-passing architecture limits parallelization and scaling, which further highlights the omission of this analysis in the current paper.\n\nReferences:\n[1] K. T. Schütt, H. E. Sauceda, P.-J. Kindermans, A. Tkatchenko, and K.-R. Müller, \"SchNet – A deep learning architecture for molecules and materials,\" *The Journal of Chemical Physics*, vol. 148, no. 24, p. 241722, 2018. https://doi.org/10.1063/1.5019779\n[2] L. Zhang, J. Han, H. Wang, R. Car, and W. E, \"Deep Potential Molecular Dynamics: A Scalable Model with the Accuracy of Quantum Mechanics,\" *Physical Review Letters*, vol. 120, no. 14, p. 143001, 2018. https://doi.org/10.1103/PhysRevLett.120.143001\n[3] A. Musaelian, S. Batzner, A. Johansson, L. Sun, C. J. Owen, M. Kornbluth, and B. Kozinsky, \"Learning local equivariant representations for large-scale atomistic dynamics,\" *Nature Communications*, vol. 14, p. 579, 2023. https://doi.org/10.1038/s41467-023-36329-y", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|5|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb5", "comment": "The claim that NequIP requires \"orders of magnitude fewer training data\" is not rigorously supported because the comparison with DeepMD is unfair (comparing NequIP trained on 133 samples against DeepMD trained on 133,500 samples) and lacks a direct control experiment.\n\n\"NequIP outperforms existing models with up to three orders of magnitude fewer training data, challenging the widely held belief that deep neural networks require massive training sets.\" (Abstract)\nThis is a very strong claim that requires rigorous evidence. The paper attempts to support this by comparing NequIP's performance on a small dataset with DeepMD's performance on a large dataset, rather than comparing both on the same small dataset.\n\"Table III shows the comparison of the predictive force accuracy of NequIP trained on the 133 structures vs DeepMD trained on 133,500 structures. We find that with 1000x fewer training data, NequIP significantly outperforms DeepMD on all four parts of the data set.\" (Liquid Water and Ice Dynamics section)\nTable III compares NequIP (133 samples) with DeepMD (133,500 samples). This comparison is flawed because it does not show how DeepMD performs on 133 samples. It is possible that DeepMD would perform poorly, but without that data point, the \"orders of magnitude\" claim is an inference based on the assumption that DeepMD *needs* 133,500 samples to reach that performance, which is not proven. A fair comparison would involve training DeepMD (and other baselines) on the same 133 samples to demonstrate the specific advantage of NequIP in the low-data regime.\n\"We further note, that in [39], a Behler-Parrinello Neural Network (BPNN) was trained on 1303 structures... We find that NequIP models trained with as little as 50 and 100 data points obtain RMSEs...\" (Data Efficiency section)\nThe comparison with BPNN [4] is made across different papers with potentially different data splits and evaluation protocols (\"evaluated on the remaining 290 structures\" for BPNN vs \"on their respective test sets\" for NequIP). This lacks the rigor of a controlled side-by-side comparison on the same data splits.\n\nReferences:\n[4] B. Cheng, E. A. Engel, J. Behler, C. Dellago, and M. Ceriotti, \"Ab initio thermodynamics of liquid and solid water,\" *Proceedings of the National Academy of Sciences*, vol. 116, no. 4, pp. 1110–1115, 2019. https://doi.org/10.1073/pnas.1815117116", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|5|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb5", "comment": "The paper reports performance metrics (MAE/RMSE) as single values without uncertainty quantification (e.g., standard deviation over multiple runs), which is critical given the small dataset sizes used in the experiments.\n\n\"The mean absolute error in the force components is shown in Table I in units of [meV/\\AA].\" (MD-17 small molecule dynamics section)\nTable I reports single MAE values for NequIP and baselines. When training on small datasets (e.g., 1,000 structures), the model's performance can be highly sensitive to the specific random split of the data and the weight initialization. Without error bars or standard deviations obtained from multiple independent training runs, it is difficult to assess the statistical significance of the reported improvements, especially where the differences are small (e.g., Toluene: 4.4 vs 6.1 meV/A).\n\"Table III shows the comparison of the predictive force accuracy of NequIP trained on the 133 structures vs DeepMD trained on 133,500 structures.\" (Liquid Water and Ice Dynamics section)\nSimilarly, Table III reports single RMSE values for a model trained on only 133 structures. The variance in performance is likely high in such a low-data regime. Reporting the mean and standard deviation over multiple folds or seeds is standard practice to ensure the robustness of the results.\n\"We measure the Li diffusivity in ten Nequip-driven MD simulations... We find a mean diffusivity of 1.42 x 10^-5 cm^2/s... thus achieving a relative error of as little as 3%.\" (Lithium Phosphate Amorphous Glass Formation section)\nWhile the authors perform multiple MD simulations to estimate diffusivity, they do not report the uncertainty (e.g., standard deviation) of the diffusivity estimate itself, only the mean. Furthermore, the training of the model itself seems to be a single run, so the uncertainty arising from the model training process is not quantified.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|5|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb5", "comment": "The evaluation on complex material systems (Formate on Cu and Li4P2O7) lacks comparison with other ML-IP baselines, making it difficult to contextualize the performance and verify the claim of \"state-of-the-art accuracy\" for these specific systems.\n\n\"The MAE of the predicted forces using a NequIP model trained on 2,500 structures is shown in Table IV demonstrating that NequIP is able to accurately model the interatomic forces for this complex reactive system.\" (Heterogeneous catalysis of formate dehydrogenation section)\nTable IV presents only NequIP's performance. Without comparing to other methods (e.g., SchNet, DeepMD) on the same dataset, it is impossible to determine if this performance is truly \"state-of-the-art\" or if simpler models could achieve similar accuracy. The paper claims to be accurate \"compared to existing ML-IP methods across a wide variety of systems\" (Introduction), but this comparison is absent for the material systems.\n\"Table V shows the test set error in the force components on both the test set from the AIMD molten trajectory and the full AIMD quenched glass trajectory.\" (Lithium Phosphate Amorphous Glass Formation section)\nSimilarly, Table V only reports NequIP's results. The lack of baselines weakens the argument that NequIP is uniquely capable of handling these complex systems compared to existing approaches.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|5|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb5", "comment": "In the comparison of MD17 performance shown in table I, indeed the NequIP shows indeed an amazing performance. Nevertheless, in the comparison to other approached including NequIP(I=0)=SchNet, the discussion reads somehow flat (what is being told is just reading table I). Here, a more insightful discussion should be added, such as elaborating on the core differences between the compared methods and explain why a neural net of this nature can outperform even kernel methods.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|5|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb5", "comment": "Additionally, to support some claims in the paper, the authors should add the performance of the of SchNet in Fig. 7 as a reference. This will greatly help the narrative of the article.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|5|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb5", "comment": "Something that will immediately capture readers attention is why only forces are being compared against other models while in all the cited references there is always a comparison of both, total energies and forces. Furthermore, there is no discussion or arguments of why the authors only train the model on forces, while there are methods in the literature that even use energies and stress tensors for training on top of forces. Everything needs to be justified. To address these issues, the comparison of energies and forces against other methods must be in the article, otherwise it could send the wrong message to the reader, meaning that the energy predictions are not accurate enough in this model (NequIP).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|5|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb5", "comment": "On the applications side, the authors show two interesting examples, Lithium Thiophosphate (LiPS) and Lithium Phosphate (Li4P2O7). Table V summarizes the training performances for MAE of the forces. Interestingly, the learning capacity (according to this measure) is reached at 2500 training points for LiPS, converging to ~24 meV/A. This is actually a good error compared to other reported methodologies. Nevertheless, it is well known that the MAE gives a good overview of the general performance of the model, but it softens the error implications of outliers. It would be more illustrative to present both performances, MAE and RMSE, given that comparing the differences between these two measures provide some degree of insights to monitor large errors on individual samples (local environments). Again, a complete evaluation of the learning performance of the method is not possible given that the energy errors are not reported.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|5|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb5", "comment": "Regarding the comparison between the dynamics using AIMD and NequIP-MD, Fig. 5 shows a really nice agreement. Just as a sanity check, I would add a simulation of NequIP-MD for a longer simulation time (500 ps, this should not be a problem for a ML model since they usually take a couple of ms per prediction as shown in Table VII) just to be sure that the simulation remains stable and reliable. Then report its g(r) in Fig. 5 as comparison. I understand that they could differ a bit.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|5|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb5", "comment": "In the case of Li4P2O7, I cannot give a proper evaluation of the application if the RMSE are missing but more importantly, because of the missing energy errors. The energetics in diffusion is crucial, and because of this, I’m not sure how to judge the reported diffusivity values. Furthermore, this application needs a convergence analysis (diffusivity vs length of the simulations) since 50 ps is an extremely short time for such a macroscopic variable. Hence, in order to discard any possible artefacts of the NequIP, such analysis should be provided.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|5|Human_1|9", "source": "prb", "split": "test", "paper_id": "prb5", "comment": "The results provided in Fig. 7 are very revealing and show the great impact of using equivariant internal features. It would give a further insight on the efficacy of the model if also l=2 is included in this example. This should definitively evince the need of such architectures in force fields reconstruction.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|5|Human_1|10", "source": "prb", "split": "test", "paper_id": "prb5", "comment": "The DISCUSSION section, does not present any discussion, it is more like a summary or conclusions. This section should be intended to present an insightful but compact discussion of the current state-of-the-art of the field and why and how your methodology actually advances the field (ML force fields) and what practitioners would gain if they use it.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|5|Human_1|12", "source": "prb", "split": "test", "paper_id": "prb5", "comment": "At the moment, the presentation of the article is more appropriate for a computational physics/chemistry journal, given that it introduces the method (which mostly was already introduced in previous publications), then present comparisons to known methods and datasets (no insightful or revealing arguments are given only numerics), and then applications, which are very interesting but need further analysis to show the reliability of the method.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|5|Human_1|13", "source": "prb", "split": "test", "paper_id": "prb5", "comment": "The biggest concern is the fact that the energy part of the model is missing, even though the main predictor of the network is indeed the energy (eq. 3). Furthermore, total energy analysis is a standard measure of accuracy in the field, hence this shows that the work is not complete.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|5|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb5", "comment": "I am a bit confused by Eqn.5: does it mean that the interacting force vector between two atoms i and j is only dependent on the displacement rij? But one would expect that the force also depends on the other atoms close to i and j. Presumably such many-body effects are considered during the convolution step, but this is not clear from Eqn.5.", "reviewer_type": "human", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|5|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb5", "comment": "Page 9, line 446: The authors wrote \\\"ability to achieve high accuracy on a comparatively small data set opens the door to training models on expensive high-order ab-initio quantum chemical methods.\\\" This seems to be a bit overstated, as previous MLPs that trained on CCSD(T) and QMC already exist.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|5|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb5", "comment": "Although it is very impressive that the authors are able to train a MLP for water with 1000x fewer training data compared to DeepMD, bear in mind that the first generation of DeepMD (the un-smooth version) is highly data-inefficient due to the \\\"cusps\\\" introduced by the permutations of atoms. Also the water data set contains the whole MD trajectory, meaning that the training data is highly correlated so significant sparsification can be done before hampering the amount of information contained in the data set. I suggest that the authors consider including these more nuanced points, so that readers who are not familiar with the field won't be misled.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|5|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb5", "comment": "Some discussions on how the atomic cutoffs and the number of convolutions affect the results can be very helpful to readers.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|5|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb5", "comment": "The idea of learnable radial functions in the decomposition of the convolution filters presented in Eq. (5) is an interesting one. Could the authors provide some justification for why it is necessary to learn these using a small NN as opposed to simply expanding them in a basis set or as a polynomial and then learning the coefficients of each as part of the overall training scheme. This idea has been investigated for learning activation functions in neural networks [see, for example, Goyal, et al. 101, 1-18 (2019)]. Wouldn't this be an easier scheme overall?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|6|Claude|1", "source": "prb", "split": "test", "paper_id": "prb6", "comment": "The paper claims that \"no significant differences between the two groups exposed at 11.7T and 0T could be identified\" in safety-related measurements, yet no statistical power analysis is provided to determine whether the sample size of 20 subjects per group was adequate to detect meaningful differences, raising concerns about whether the absence of statistical significance reflects true safety or simply insufficient power.\n\n\"Twenty volunteers (24.2±4.8 year old, 8 males) were scanned at 11.7T and performed the tests mentioned below. Another set of twenty volunteers (23.6±6.0 year old, 7 males) was exposed to a 0T, nocebo, field and underwent the same tests (except genotoxicity).\"\nThe study uses only 20 subjects per group for safety assessment. For a first-in-human safety study at such an unprecedented field strength, this sample size is notably small. Without a power analysis, readers cannot determine whether the study was adequately powered to detect clinically meaningful differences in physiological, vestibular, or cognitive measures between groups. The absence of detectable differences could reflect either true safety equivalence or simply Type II error due to inadequate statistical power.\n\"In all tests performed throughout the protocol, no significant differences between the two groups exposed at 11.7T and 0T could be identified (extended data Fig. 3 and Table 1).\"\nThe authors interpret the lack of statistical significance as evidence for safety. However, in statistical hypothesis testing, failure to reject the null hypothesis does not confirm the null hypothesis—particularly when power is unknown. Standard practice in safety studies would include equivalence or non-inferiority analyses with predefined margins, or at minimum, report power calculations showing adequate sensitivity to detect effects of concern.\n\"Methods: A total of 29 subjects were exposed to a 10.5 T MRI field and underwent vestibular, cognitive, and physiological testing before, during, and after exposure; for 26 subjects, testing and exposure were repeated within 2-4 weeks of the first visit.\" [[1]](#citation-1)\nThe comparable 10.5T safety study by Grant et al. (2020) used a larger sample size (29 subjects) and implemented a repeated-measures design where 26 subjects underwent testing twice with 2-4 weeks separation. This design provides substantially more statistical power through within-subject comparisons and enables assessment of short-term versus longer-term effects. The current study's single-visit design with fewer subjects represents a less rigorous approach to safety assessment.\n\nReferences:\n[1] Grant, A., Metzger, G.J., Van de Moortele, P.F., et al. \"10.5 T MRI static field effects on human cognitive, vestibular, and physiological function.\" Magnetic Resonance Imaging 73, 163-176 (2020). https://pubmed.ncbi.nlm.nih.gov/32822819/", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|6|Claude|2", "source": "prb", "split": "test", "paper_id": "prb6", "comment": "The genotoxicity assessment was performed only for the 11.7T group using before/after intra-subject comparisons without a 0T control group, which is methodologically inconsistent with how other safety measures were evaluated and may be insufficient given that prior literature has demonstrated genotoxic effects from repeated MRI exposure.\n\n\"Genotoxicity was also assessed but only for the 11.7T group with blood samples drawn before and after the 90 min exposure to perform intra-subject comparisons.\"\nWhile the behavioral, vestibular, and physiological tests included both 11.7T and 0T control groups for between-group comparisons, the genotoxicity assessment inexplicably omits the 0T control group. This creates an asymmetry in the study design where arguably the most concerning potential safety outcome (genetic damage) receives less rigorous evaluation than other measures. An intra-subject pre/post design without a control group cannot account for time-dependent changes or procedural effects unrelated to magnetic field exposure.\n\"No statistically significant differences in micronuclei count for genotoxicity for each subject before versus after exposure at 11.7T were found either.\"\nThe absence of statistical significance in micronuclei counts from a single 90-minute exposure in 20 subjects has limited interpretability. Reference [15] cited in the paper (Herate et al., 2022 [[4]](#citation-4)) specifically examined effects of \"repeated brain MRI\" at 3T. The current study's single-exposure design may be insufficient to detect cumulative genotoxic effects that could emerge with the repeated exposures typical of clinical or research MRI use. The authors cite this reference but do not adequately address why single-exposure testing is sufficient given the documented effects from repeated exposures.\n\"Having shown that the repetitive exposure to 3T in MRI [15] induces mainly terminal deletions, the micronuclei protocol was performed with cytochalasin B addition at 68h after lymphocyte growth stimulation\"\nThe authors acknowledge that their reference [15] demonstrated genotoxic effects from repeated MRI exposure. However, the study design tests only single exposure, which does not address whether repeated 11.7T exposures would produce similar or enhanced effects. Given that chronic or repeated exposure has been identified as the relevant exposure scenario for genotoxicity concerns, the single-exposure design represents a significant gap in the safety assessment.\n\nReferences:\n[4] Herate, C., Brochard, P., De Vathaire, F., et al. \"The effects of repeated brain MRI on chromosomal damage.\" European Radiology Experimental 6, 12 (2022). https://link.springer.com/article/10.1186/s41747-022-00264-2", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|6|Claude|3", "source": "prb", "split": "test", "paper_id": "prb6", "comment": "The paper claims superior signal-to-noise ratio at 11.7T compared to 3T and 7T, but provides only visual comparison of images acquired from different subjects using different RF coil configurations, without any quantitative SNR measurements to support the claim.\n\n\"A 2D T2*-weighted acquisition was repeated with the same protocol (resolution, bandwidth, acquisition time, number of receive elements) at 3T and 7T on different volunteers. The comparison highlights the gain in signal:noise ratio (SNR) at 11.7T\"\nThe authors explicitly acknowledge using \"different volunteers\" for the cross-field comparison. Inter-subject variability in brain anatomy, tissue composition, and physiological noise is well-documented in MRI literature and can significantly confound comparisons. While matching acquisition parameters is appropriate, subject-to-subject variability can introduce substantial differences in image quality that are unrelated to field strength. A rigorous comparison would require within-subject measurements or use of standardized phantoms.\n\"Acquisitions were performed with 1Tx (body coil)-32Rx, 8Tx-32Rx and 8Tx-32Rx head coils at 3T, 7T and 11.7T respectively.\"\nThe RF coil configurations differ significantly across field strengths (1Tx body coil at 3T versus 8Tx dedicated head coils at 7T and 11.7T). Transmit coil efficiency, receive coil geometry, and channel count all substantially affect SNR independent of field strength. The use of a body coil for transmission at 3T versus optimized parallel transmit head coils at higher fields introduces additional confounds beyond field strength that are not accounted for in the comparison.\n\"The comparison highlights the gain in signal:noise ratio (SNR) at 11.7T, which can be traded for higher spatial (or temporal) resolutions\"\nDespite claiming SNR gains, the paper provides no quantitative SNR measurements. Standard MRI literature reports SNR values using established methodologies (e.g., signal from tissue regions divided by noise from background or difference images). The claim of \"supralinear gain in sensitivity\" referenced from prior work [[2]](#citation-2) was based on quantitative measurements. The current paper's visual comparison in Figure 2C, while visually compelling, does not provide the quantitative evidence needed to substantiate SNR claims or enable comparison with published values at other field strengths.\n\"The SNR was measured at the center of a spherical water saline phantom with a gradient‐recalled echo sequence. Measurements were performed at NeuroSpin at 3, 7, and 11.7 T.\" [[3]](#citation-3)\nNotably, the same research group published a rigorous quantitative SNR comparison (Le Ster et al., 2022) using phantom measurements with controlled experimental conditions across field strengths. This methodology, which yielded precise SNR scaling data (B₀^1.94±0.16), would have been directly applicable to the current in vivo study. The absence of similar quantitative measurements in the current paper, despite the group's demonstrated capability, represents a missed opportunity to provide objective evidence for the claimed SNR benefits.\n\nReferences:\n[2] Pohmann, R., Speck, O., Scheffler, K. \"Signal-to-noise ratio and MR tissue parameters in human brain imaging at 3, 7, and 9.4 tesla using current receive coil arrays.\" Magnetic Resonance in Medicine 75, 801-809 (2016). https://onlinelibrary.wiley.com/doi/10.1002/mrm.25677\n[3] Le Ster, C., Grant, A., Van de Moortele, P.F., et al. \"Magnetic field strength dependent SNR gain at the center of a spherical phantom and up to 11.7T.\" Magnetic Resonance in Medicine 88, 2131-2138 (2022). https://pubmed.ncbi.nlm.nih.gov/35849739/", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|6|GPT|1", "source": "prb", "split": "test", "paper_id": "prb6", "comment": "This paper draws overly strong conclusions about human safety/tolerability at 11.7T from a small, short-term, endpoint-limited protocol, which weakens the validity of the safety claims made in the Abstract and Main text.\n\n\"To assure the safety of human imaging at such high field strength, we performed physiological, vestibular, behavioral and genotoxicity measurements on the volunteers. The data shows no evidence of adverse effects.\" \nThis pair of sentences is used to justify a broad safety conclusion, but “no evidence of adverse effects” is a non-equivalence statement that depends strongly on sample size, endpoint sensitivity, and follow-up duration. The described measures target a subset of plausible acute and subacute effects, but do not address detection of rare events or delayed outcomes, which is central when translating a first-in-human ultra-high-field exposure into a generalized “safety” assertion. The paper does not report an a priori safety endpoint hierarchy, minimally important differences, or any power/sensitivity analysis for the bioeffects outcomes, so readers cannot assess what magnitude of harm the study could have detected. In MRI safety contexts, the field’s novelty (11.7T whole-body) raises the bar for evidentiary strength, because the appropriate inference is typically “no concerning signal observed under this protocol” rather than “safe” in general. As written, the conclusion materially overreaches what the reported study design can support.\n\"Twenty volunteers (24.2±4.8 year old, 8 males) were scanned at 11.7T and performed the tests mentioned below.\" \nA cohort of 20 healthy young adults is a reasonable starting point for feasibility, but it is not sufficient to substantiate broad claims about safety and innocuousness of 11.7T scanning, particularly for outcomes that may be infrequent or heterogeneous across populations. The inclusion criteria (18–40 years) also intentionally narrow the population, which further limits external validity of the “humans can safely tolerate” implication. The manuscript does not provide a rationale that this N is adequate for the multiple physiological, vestibular, cognitive, and genotoxicity endpoints it assesses. Without a quantitative sensitivity/power discussion, the negative findings are hard to interpret because the study could simply be underpowered for clinically meaningful or rare effects. In safety-focused first-in-human work, it is standard to explicitly frame conclusions as preliminary and bounded by the sample and follow-up.\n\"Randomised trials offer the best approach for providing safety data as well as efficacy data, although they cannot detect rare harms.\" [[5]](#cite-5)\nThis statement highlights a core limitation of using small human studies to infer safety: even rigorous randomized designs are structurally limited in detecting rare adverse events. The present paper’s safety assessment is based on two cohorts of 20 participants and is not positioned as an adequately powered harms-detection study, making the “no adverse effects” framing particularly vulnerable to false reassurance. The issue is amplified because the paper does not quantify uncertainty around adverse-event rates (e.g., confidence bounds) or specify which harms were actively adjudicated versus passively reported. The quoted guidance is consistent with common practice that early studies can screen for frequent/large effects but cannot establish absence of uncommon harms. Therefore, the manuscript’s broad safety conclusion is not justified by its study scale.\n\"Authors should particularly avoid the common error of interpreting a non-significant result as indicating equivalence of interventions.\" [[5]](#cite-5)\nThe paper repeatedly interprets “no significant differences” between 11.7T and 0T as evidence for innocuousness, but the statistical non-significance of group differences does not establish equivalence without an explicit equivalence/non-inferiority design and margins. The manuscript does not report equivalence margins, confidence intervals for group differences, or an analysis plan tailored to equivalence, so its interpretation risks precisely the error described in the CONSORT elaboration. This is not a cosmetic reporting issue: it directly affects whether the central safety conclusion is logically warranted. In safety studies, equivalence-style reasoning is often crucial because the claim of “no effect” must be defined quantitatively. The absence of that framework makes the conclusion unreliable.\n\"Likewise, a relatively large p-value does not imply evidence in favor of the null hypothesis; many other hypotheses may be equally or more consistent with the observed data.\" [[2]](#cite-2)\nThe manuscript’s safety narrative leans heavily on finding no statistically significant differences between groups and then describing the impact of field exposure as “negligible,” but the cited principle warns against that inference. A large p-value is compatible with a wide range of effect sizes when the study is small or measurements are noisy, which is exactly the situation for many physiological and behavioral endpoints in N=20 cohorts. The paper does not present confidence intervals for key endpoints or a structured equivalence analysis, so the reader cannot tell whether clinically meaningful differences have been excluded. In MRI safety evaluation, the magnitude and uncertainty of effects matter at least as much as whether a threshold is crossed, because small effects may still accumulate or interact with other stressors. This mismatch between statistical interpretation best practices and the manuscript’s conclusions undermines the robustness of its “no adverse effects” messaging.\n\"A modified testing protocol informed by these results was devised with the goal of permitting increased enrollment while providing continued monitoring to evaluate field effects.\" [[4]](#cite-4)\nThis prior ultra-high-field study (10.5T) illustrates a more cautious and methodologically standard posture: initial observations are treated as preliminary signals that motivate larger enrollment and continued monitoring, rather than being used to broadly confirm safety. The contrast matters because the paper under review claims that its “safety and imaging data” confirm applicability and that “humans can safely tolerate” 11.7T, despite having a comparable or smaller cohort than other UHF safety pilots. The quoted sentence evidences a field norm that early UHF human exposure studies remain vigilant to subtle or low-frequency effects and explicitly plan follow-on monitoring to strengthen inference. That norm is especially relevant at 11.7T, where multiple physiological systems (vestibular, cognitive, cardiovascular, thermal) could be affected. Compared to this practice, the reviewed paper’s conclusion is stronger than its evidentiary base.\n\nReferences:\n[2] Wasserstein RL, Lazar NA. *The ASA’s statement on p-values: context, process, and purpose*. The American Statistician (2016). https://sciences.ucf.edu/biology/d4lab/wp-content/uploads/sites/23/2017/03/WassersteinLazar2016.pdf\n[4] Grant A, Metzger GJ, Van de Moortele P-F, et al. *10.5 T MRI static field effects on human cognitive, vestibular, and physiological function* (Abstract). PubMed (PMID: 32822819). https://pubmed.ncbi.nlm.nih.gov/32822819/\n[5] Moher D, Hopewell S, Schulz KF, et al. *CONSORT 2010 Explanation and Elaboration: updated guidelines for reporting parallel group randomised trials* (PDF). BMJ (2010). https://www.bmj.com/content/bmj/340/bmj.c869.full.pdf", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|6|GPT|2", "source": "prb", "split": "test", "paper_id": "prb6", "comment": "This paper’s conclusion that 11.7T provides a higher SNR (and related contrast-to-noise benefits) is not robustly supported because the 3T/7T/11.7T comparisons are performed on different subjects and different transmit/receive configurations, and no quantitative SNR/CNR measurement protocol is reported for the comparison.\n\n\"A 2D T2*-weighted acquisition was repeated with the same protocol (resolution, bandwidth, acquisition time, number of receive elements) at 3T and 7T on different volunteers. The comparison highlights the gain in signal:noise ratio (SNR) at 11.7T...\" \nThe paper uses a cross-subject comparison to argue a field-strength-driven SNR gain, but SNR is sensitive to subject anatomy/positioning, motion, and physiological noise, so “different volunteers” introduces an uncontrolled confound. The text also limits “same protocol” to a subset of parameters, leaving other contributors (coil loading, shimming success, flip-angle accuracy, reconstruction settings) potentially different across sites/systems. Because the comparison is not within-subject and the paper does not present quantitative SNR estimation (with uncertainties), the evidence is largely qualitative and cannot cleanly attribute observed differences to B0. In standard MRI methodology, field-strength SNR comparisons are typically designed to isolate B0 effects by holding subjects and coil geometry as constant as possible. As written, the paper’s phrasing overstates causal attribution from an under-controlled comparison.\n\"Acquisitions were performed with 1Tx (body coil)-32Rx, 8Tx-32Rx and 8Tx-32Rx head coils at 3T, 7T and 11.7T respectively.\" \nThis sentence directly indicates that the transmit chain differs substantially across field strengths (body-coil transmit at 3T versus multi-channel transmit at 7T/11.7T), which alters flip-angle uniformity and achievable signal even at fixed nominal sequence parameters. Coil design is a major determinant of receive sensitivity and parallel imaging behavior, so changing coil type makes it difficult to attribute differences to B0 alone. The paper does not provide a calibration/normalization method to separate coil-related gains from field-strength gains (e.g., intrinsic SNR modeling, flip-angle correction, or controlled phantom normalization). In ultra-high field, coil performance and B1 inhomogeneity are known to be major limiting factors, making this confound especially consequential. Therefore, the claimed field-strength “gain in SNR” is not methodologically well supported.\n\"The same human subjects were scanned at all three field strengths, using identical sequence parameters and similar 31- or 32-channel receive coil arrays.\" [[3]](#cite-3)\nThis published field-strength comparison provides a clear methodological contrast: it removes major confounds by scanning the same subjects and using matched acquisition parameters and comparable receive arrays. That design choice is widely regarded as necessary to make credible statements about how SNR scales with B0 in vivo, because it limits inter-subject variability and coil-related effects. The reviewed paper explicitly does the opposite (different subjects and different transmit strategies), so its evidence does not reach the rigor level commonly expected for quantitative SNR claims. Importantly, the literature example shows that controlling these factors is feasible and standard for SNR scaling studies, undermining any implication that qualitative cross-subject figures are sufficient. This gap weakens the reliability of the manuscript’s interpretation.\n\"The g-factors did not show the expected decrease, indicating a dominating role of coil design.\" [[3]](#cite-3)\nThis result emphasizes that hardware (especially coil design) can dominate performance metrics even when field strength changes, which directly bears on the reviewed paper’s use of different coil/transmit configurations at 3T/7T/11.7T. If coil design can dominate acceleration penalties and effective sensitivity, then attributing observed image differences to B0 without a controlled design is unreliable. The reviewed paper does not report g-factor, SNR maps, or reconstruction comparability across systems, so the potential coil-dominance confound remains unaddressed. This is a major issue because the paper’s broader claims about “high signal and contrast to noise ratio” at 11.7T implicitly point to B0 as the primary cause. The literature indicates that without controlling or quantifying coil effects, such causal claims are not robust.\n\nReferences:\n[3] Pohmann R, Speck O, Scheffler K. *Signal-to-noise ratio and MR tissue parameters in human brain imaging at 3, 7, and 9.4 tesla using current receive coil arrays* (Abstract). PubMed (PMID: 25820458). https://pubmed.ncbi.nlm.nih.gov/25820458/", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|6|GPT|3", "source": "prb", "split": "test", "paper_id": "prb6", "comment": "The manuscript’s methodological reporting is insufficient to evaluate whether the claimed SAR mitigation and pTx safety control are robust across subjects, because key safety-relevant quantities (e.g., achieved SAR margins, hotspot validation, and sensitivity to motion) are not presented for the 11.7T pTx protocols.\n\n\"We deployed parallel transmission tools to mitigate the radiofrequency field inhomogeneity problem and tame the specific absorption rate.\" \nThis statement links the main technical contribution (pTx) to a core human safety requirement (SAR control), but it is presented as a high-level assertion without the quantitative details necessary for independent evaluation. At ultra-high field, SAR limitations and local hotspots are among the primary safety constraints, so a reader needs to see at least the operational SAR limits used, how conservatism was set, and how compliance was verified in vivo. The paper later mentions virtual observation points and constrained pulse design, but does not provide the actual SAR values (global/head SAR and local 10g SAR), margins to limits, or per-subject distributions that would substantiate “tamed” SAR. Because the safety conclusion depends on this control being reliable for all scanned subjects, the lack of quantitative reporting undermines the credibility of the safety claim. This is a methodological transparency gap that directly affects validity.\n\"The GRAPE pulse was a universal RF pulse [28] and was designed offline on a database constituted of the 6 first subject field maps.\" \nA universal pulse designed from a limited database can be practical, but it raises two safety-relevant questions: how robust is it to out-of-distribution anatomy/positioning, and how conservative are the SAR constraints under variability. The manuscript does not report any validation results showing that the universal pulse maintained SAR compliance and flip-angle targets across the remaining subjects beyond the six used to design it. In pTx, performance robustness and SAR robustness are not guaranteed to coincide; a pulse can appear to work (acceptable flip-angle error) while still creating higher local SAR hotspots in some anatomies. Without reporting robustness statistics or worst-case analyses, readers cannot judge whether the approach generalizes safely beyond the design set. This is particularly important because the paper’s conclusions generalize to “humans” rather than to the six-map database.\n\"It enables spatial field manipulation, but at the same time, it may create hotspots by focusing the RF fields. This means that accurate subject-specific SAR measurement is mandatory to operate pTx appropriately.\" [[1]](#cite-1)\nThis safety review summarizes a widely accepted concern in high-field pTx: hotspot creation is an intrinsic risk, and safe operation depends on accurate (often subject-specific) SAR assessment. The reviewed paper does not report subject-specific SAR verification, nor does it describe any empirical validation (e.g., temperature monitoring or phantom verification) that would allow independent assessment of SAR modeling accuracy at 11.7T. While the paper mentions virtual observation points, it does not show how conservative the VOP set was, what head models were used, or whether model mismatch was accounted for. Given the “mandatory” nature of accurate SAR assessment emphasized in the literature, omission of these details is a major methodological gap rather than a minor reporting choice. Consequently, the reader cannot verify that the pTx approach was safely controlled across participants.\n\"They compared conventional quadrature excitation and multi-spoke parallel-transmit excitation after RF shimming and found that the local SAR increased by more than 100% in 1 and 4 cm3 for quadrature and parallel-transmit excitation, respectively, in the worst case where the head model was shifted by 20 and 10 mm in right and posterior directions, respectively.\" [[1]](#cite-1)\nThis quoted finding highlights that relatively plausible head-position changes can dramatically increase local SAR under pTx, which is directly relevant for a 90-minute session where motion is likely. The reviewed paper acknowledges motion problems for image quality but does not connect motion to SAR safety, and it does not report how head stabilization and motion were handled from a safety standpoint. Without a motion-sensitivity analysis or conservative SAR margins that explicitly account for potential motion, the claim that SAR was “tamed” is not fully supported. In ultra-high-field first-in-human studies, demonstrating safety robustness to realistic deviations (including motion) is an important part of safety reporting. The absence of this analysis reduces confidence that the protocol is safe beyond idealized conditions.\n\nReferences:\n[1] Okada T, Akasaka T, Thuy DHD, Isa T. *Safety for Human MR Scanners at 7T*. Magnetic Resonance in Medical Sciences (2022). https://pmc.ncbi.nlm.nih.gov/articles/PMC9618930/", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|6|GPT|4", "source": "prb", "split": "test", "paper_id": "prb6", "comment": "The paper’s causal interpretation that observed bioeffects outcomes reflect “no effect of field exposure” (rather than psychological or procedural confounds) is weakened by the non-randomized sequential cohort design and limited reporting on blinding effectiveness and protocol stability.\n\n\"Those tests were performed on the 20 subjects scanned at 11.7T and on another cohort of 20 subjects with the magnetic field switched off, to disentangle any effect from a possible psychological bias (nocebo effect).\" \nThe manuscript explicitly frames the 0T cohort as enabling causal disentanglement of field effects from psychological bias, which is a strong claim that typically requires careful control of allocation, blinding, and protocol stability. However, the paper does not report objective checks of blinding success (e.g., whether subjects correctly guessed condition, or whether staff were blinded) beyond stating that participants were not informed. It also does not report whether any protocol elements changed over time (e.g., operator practice, task instructions, sequence tweaks) that could differentially affect the first and second cohort. Because “nocebo disentanglement” is a central support for the safety conclusion, these missing design/reporting elements weaken the internal validity of the comparison. In the absence of such controls, “no significant differences” is consistent with multiple alternative explanations beyond “no field effect.”\n\"To minimize the number of field ramps for the magnet, the study first included the 0T group, followed by the 11.7T one.\" \nThis sentence makes clear that group assignment was not randomized and that the cohorts were run in a fixed order, which introduces temporal confounding (learning effects in operators, protocol drift, seasonal/organizational changes, or differing recruitment). In biomedical research, non-randomized sequential allocation can bias group comparisons even when baseline demographics appear similar, particularly for behavioral and subjective endpoints. The manuscript does not provide mitigation strategies for this design choice (e.g., alternating conditions, pre-registered analysis, or sensitivity analyses), nor does it present evidence that measurement conditions were stable across the study period. Because the core inference is based on between-group differences (11.7T vs 0T), the fixed-order design reduces the credibility of the causal claim. This is a substantial internal-validity limitation rather than a minor procedural detail.\n\"Vertigo was apparently more frequent and severe at 7T, but unpleasantness by moving in and out of the scanners was noted even at 0T, although the severity was higher at 7T. Moreover, five subjects noticed mild magnetic field at 0T.\" [[1]](#cite-1)\nThis literature quote demonstrates two problems that directly apply to the reviewed paper’s nocebo-control logic: (i) subjective discomfort can occur even in 0T mock conditions, and (ii) participants may infer (correctly or incorrectly) field presence, compromising blinding. The reviewed paper tries to mimic gradient noise and keep subjects uninformed, but it does not report whether subjects detected the condition or whether expectancy differed between cohorts. The literature indicates that such factors can materially influence subjective and behavioral outcomes, meaning that simple “0T + same instructions” may be insufficient to fully isolate nocebo effects. This matters because the paper’s conclusion hinges on the idea that psychological bias is neutralized by design. Without explicit checks, the disentanglement claim is not well supported.\n\"Proper randomisation reduces selection bias at trial entry and is the crucial component of high quality RCTs.\" [[5]](#cite-5)\nWhile the reviewed study is not a therapeutic RCT, it makes a causal claim that depends on between-group comparability, which is exactly the context where randomization is the standard bias-reduction tool. The paper’s stated reason for fixed ordering (minimizing field ramps) is operationally understandable, but it does not address the resulting risk of bias in interpreting group differences as field effects. The CONSORT elaboration emphasizes that without randomization, selection and confounding biases can prejudice comparisons, especially when outcomes include subjective experiences and cognitive task performance. The reviewed manuscript’s reporting does not include compensatory design features (e.g., cross-over design, counterbalancing, or randomized assignment) that would restore the strength of the causal inference. Therefore, the claimed separation of nocebo and field effects is methodologically weaker than presented.\n\nReferences:\n[1] Okada T, Akasaka T, Thuy DHD, Isa T. *Safety for Human MR Scanners at 7T*. Magnetic Resonance in Medical Sciences (2022). https://pmc.ncbi.nlm.nih.gov/articles/PMC9618930/\n[5] Moher D, Hopewell S, Schulz KF, et al. *CONSORT 2010 Explanation and Elaboration: updated guidelines for reporting parallel group randomised trials* (PDF). BMJ (2010). https://www.bmj.com/content/bmj/340/bmj.c869.full.pdf", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|6|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb6", "comment": "The manuscript fails to provide a detailed description of the imaging sequences and reconstruction methods used to acquire the \"first in vivo images\", violating reproducibility standards.\n\n\"We tackled this problem by deploying parallel transmission hardware and software, first developed by the laboratory at 7T and further optimized for 11.7T (Methods).\"\nThe \"Methods\" section referenced here is missing from the manuscript. The only methods sections present are \"Genotoxic tests\", \"Behavioral tests\", and \"Balance tests\", leaving the core imaging methodology undefined.\n\"T2 and T2*-weighted acquisitions were successfully performed by deploying the parallel transmission techniques (Fig. 2).\"\nNo sequence parameters (e.g., TR, TE, Flip Angle, Bandwidth, Matrix size, Acceleration factor) are provided for these acquisitions. Without these details, it is impossible for other researchers to reproduce the study or assess the technical quality of the images.\n\"Acquisition parameters... must be reported.\" [1]\nThe COBIDAS guidelines, a standard for neuroimaging reporting, explicitly state that full acquisition parameters must be reported to ensure reproducibility and transparency.\n\nReferences:\n[1] Nichols, T. E., et al. (2017). Best practices in data analysis and sharing in neuroimaging using MRI. Nature Neuroscience, 20(3), 299-303. https://www.nature.com/articles/nn.4500", "reviewer_type": "ai", "label": "error", "error_type": "Neglect", "label_origin": "expert+llm-filter"}
{"id": "prb|6|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb6", "comment": "The paper relies on qualitative statements to assess image quality and SNR gain, lacking quantitative metrics essential for validating the performance of the new 11.7T scanner.\n\n\"The presented in vivo human brain images acquired at 11.7T thereby reveal good signal homogeneity consistent with the simulations, without severe RF field inhomogeneity artefacts.\"\n\"Good\" is a subjective descriptor. The authors do not present B1+ maps or quantitative homogeneity metrics (e.g., coefficient of variation) for the in vivo data to objectively demonstrate the performance of the parallel transmission system at 11.7T.\n\"The comparison highlights the gain in signal:noise ratio (SNR) at 11.7T, which can be traded for higher spatial (or temporal) resolutions...\"\nNo SNR values, maps, or measurements are provided to quantify this claimed gain. A scientific comparison of field strengths requires quantitative data to substantiate claims of improvement.\n\"Signal-to-noise ratio (SNR) maps were calculated... The SNR increased supralinearly with field strength...\" [2]\nPrevious studies comparing field strengths (e.g., Pohmann et al.) provide detailed quantitative SNR maps and measurements to validate expected gains, setting a standard that this paper fails to meet.\n\nReferences:\n[2] Pohmann, R., Speck, O., & Scheffler, K. (2016). Signal-to-noise ratio and MR tissue parameters in human brain imaging at 3, 7, and 9.4 Tesla using current receive coil arrays. Magnetic Resonance in Medicine, 75(2), 801-809. https://onlinelibrary.wiley.com/doi/full/10.1002/mrm.25677", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|6|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb6", "comment": "Given the unprecedented field strength, the description of safety monitoring, particularly regarding RF heating (SAR), is insufficient.\n\n\"The specific absorption rate (SAR), also growing with Bo [10], was tamed with virtual observation points [11] and dedicated RF pulse design algorithms [12].\"\nWhile the method is named, no data is shown on the actual SAR levels monitored during the scans or the validation of the Virtual Observation Points (VOP) model at 11.7T. Given the high risk of local heating at this frequency, detailed safety data is crucial.\n\"The data shows no evidence of adverse effects.\"\nThe paper focuses on physiological and behavioral side effects but omits the technical safety data (e.g., temperature simulations vs. measurements) that would prove the RF safety of the imaging session itself.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|6|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb6", "comment": "The provided code repository only contains scripts for the behavioral task (ANT), while the core technical innovation (pTx pulse design and reconstruction) is not shared.\n\n\"We tackled this problem by deploying parallel transmission hardware and software...\"\nThe paper attributes the success of the imaging to this software, yet it is not provided.\n```\nANT-R task\n=============\n...\n`ant-r-classic.py` is a script implementing the ANT-R task described in Fan, J. et al (2009).\n```\nThe `README.md` in the provided code repository confirms that the code is exclusively for the \"Attentional Network Task\" (behavioral), not for the MRI pulse design or image reconstruction.\n\"The code repository... contains several Python scripts implementing variants of the ANT task.\"\nThe absence of the imaging code prevents reproduction of the pTx pulses and image reconstruction, which are the primary technical contributions enabling the 11.7T images.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|6|Gemini|5", "source": "prb", "split": "test", "paper_id": "prb6", "comment": "The comparison with 7T is limited to a single T2*-weighted protocol and does not benchmark against state-of-the-art 7T imaging.\n\n\"A 2D T2*-weighted acquisition was repeated with the same protocol (resolution, bandwidth, acquisition time, number of receive elements) at 3T and 7T...\"\nUsing the \"same protocol\" across field strengths is often suboptimal because relaxation times (T1, T2*) change with field strength. A fair comparison would use protocols optimized for each field strength to demonstrate the true potential of 11.7T over 7T.\n\"Images indicate sufficient SNR to boost further spatial resolution or decrease acquisition time in the future.\"\nWithout a comparison to optimized 7T images (which can also achieve very high resolution), the claim that 11.7T provides a unique advantage is not fully supported by the evidence presented.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|6|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb6", "comment": "In order to maximize the impact of this scientific report, it is important to provide open access to the initial data presented in figure 2. This will pique the curiosity of the community and greatly increase the number of citations for this study. Although the authors have stated that \\\"All data supporting the findings of this study are available within the paper and its Extended Method,\\\" I was unable to locate this information in the materials provided for review. Sharing data is now more accessible than ever through platforms like neurovault.org, which I highly recommend to the authors.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|6|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb6", "comment": "In essence, sharing the neuroimaging data displayed in figure 2 will enable the community to adopt this technological advancement with enthusiasm, scrutinize the accuracy of the findings, and pave the way for future research and discoveries. I strongly urge you to consider sharing this valuable data.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|6|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb6", "comment": "While the image resolution is certainly impressive, similar resolutions have been demonstrated using lower field strengths (7T), albeit with longer scan times, see for example Feinberg et al, “Next generation MRI scanner” Nature Methods 20, 2023. doi: 10.1038/s41592-023-02068-7.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|6|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb6", "comment": "Show images of all subjects, e.g. in the supplementary materials, to demonstrate the robustness of results or at least discuss issues with robustness at this stage.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|6|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb6", "comment": "Show results of other relevant contrasts (T1, DWI, MR angiography) and methods that are very likely to profit from 11.7T (e.g. MRS, fMRI) as well, or at least discuss issues that arise with these and other important MR contrasts.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|6|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb6", "comment": "While I understand that the authors have 3T and 7T scanners available at their facility. I would argue that the relevant reference point would be the human imaging results obtained at the field strength of 10.5T. A more detailed comparison with published findings at this field strength (closest to the one used here) would be highly relevant.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|6|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb6", "comment": "The comparison with 3T and 7T results seems biased as it is unclear if the parameters used were optimized at the lower field strengths. Acquisition parameters have not been provided, only stated that \\\"similar scans were performed\\\".", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|6|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb6", "comment": "While the authors briefly mention next steps in the technical developments, I miss a more detailed discussion of how much these will improve SNR (compared to theoretical possible SNR) and resolution (e.g. with the improved motion mitigation strategies) and other aspects.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|6|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb6", "comment": "I miss a clearer and more detailed discussion about what the current results and future developments mean for scientific/neuroscience and potentially clinical applications.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|6|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb6", "comment": "A few times ISMRM abstracts are used as references, but these seem only accessible to registrants of the conference. While most people in the field will likely have/get access, this is not the case for the average reader.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|6|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb6", "comment": "The project name Iseult is used throughout the manuscript, but it is unclear what the specific meaning is?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|6|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb6", "comment": "I think the work would benefit from a better description of state-of-the-art resolution compared to the new scanner.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|6|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb6", "comment": "In that sense I was also somewhat surprised that the authors didn’t attempt to break any “records” for resolution. For instance, doi: 10.1016/j.neuroimage.2013.08.013 acquired images at 9.4T with 0.13x0.13x0.8 mm^3 and doi: 10.1371/journal.pone.0133921 presented 0.44 mm isotropic resolution. Without robbing any novelty from the current work, it may be beneficial to at least discuss these previous works and state the highest state-of-the-art resolutions in other fields (perhaps also vis-a-vis scan time and motion effects).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|6|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb6", "comment": "In Fig 2 it is unclear which exact conditions were used in each of the 3/7/11.7 T measurements. Would they be expected to only vary in resolution (i.e. were TE/TR adjusted for the different field T2(*/T1) or were they performed under the same conditions (TE/TR)? If the latter, contrast is expected to vary, and to make a good comparison it is recommended to match the contrast conditions while only varying resolution if possible. Please clarify.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Claude|1", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "The paper's central motivation for measuring the 583 MHz transition is that it is \"isolated\" from other hyperfine transitions, which should reduce systematic line-pulling effects. However, the discovery of significant n=3 state population introduces substantial line-pulling that undermines this advantage, yet the paper still concludes this is \"the best candidate for future precision M LS measurements\" without adequately demonstrating how the proposed mitigation strategies would work in practice.\n\n\"Due to the reduced influence of other nearby transitions, the systematic uncertainties related to line-pulling would become negligible.\"\nThis statement from Section I presents the key motivation for choosing the 583 MHz transition over the other allowed transitions at 1140 MHz and 1326 MHz. The paper follows the approach of the most precise hydrogen Lamb shift measurements ([Bezginov et al., Science 365, 1007 (2019)][1]) which selected the F=0→F=1 transition specifically because it is isolated. However, the authors' own experimental results reveal that while this transition may be isolated from other n=2 hyperfine levels, it is significantly contaminated by n=3 states that were not initially considered in the measurement design.\n\"In our measurement, the comparably large population of 3S states distorts the line-shape and introduces line-pulling, which might seem to defeat the purpose of choosing the isolated n = 2 transition.\"\nThis statement from Section IV explicitly acknowledges that the supposed advantage of the isolated transition is compromised by the 3S contamination. The detected B₃S/B₂S ratio of 0.20(4) means that roughly one-fifth of the detected signal comes from n=3 states, which is substantial. The fit parameters change dramatically when 3S is included: the frequency offset shifts from -24.8(74) MHz to 2.3(68) MHz—a change of ~27 MHz that far exceeds the final quoted uncertainty of 6.8 MHz. This model dependence is critical because the correct extraction of the Lamb shift relies on proper accounting of all contributing signals.\n\"However, the n = 3 population can be electrically quenched with a weak electrical field, leaving a large fraction of the n = 2 population unharmed as shown by measurements from Bezginov et al. [41].\"\nWhile mitigation strategies are proposed, no quantitative analysis is provided to demonstrate that n=3 quenching would be effective for muonium under the specific experimental conditions (different velocity distributions, different field strengths required, etc.). The reference to Bezginov's PhD thesis concerns hydrogen, not muonium, and the quenching dynamics may differ due to the different reduced masses and level spacings. The claim that this transition is \"the best candidate for future precision M LS measurements\" would benefit from demonstrating the feasibility of the proposed 3S suppression techniques.\n\nReferences:\n[1] N. Bezginov, T. Valdez, M. Horbatsch, A. Marsman, A. C. Vutha, and E. A. Hessels, \"A measurement of the atomic hydrogen Lamb shift and the proton charge radius,\" [Science 365, 1007 (2019)](https://www.science.org/doi/10.1126/science.aau7807)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Claude|2", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "The paper reports the first measurement of the 2S hyperfine splitting (HFS) in muonium (559.6(72) MHz) and compares it to a \"theoretical value\" of 557.9 MHz with uncertainty \"<0.1 MHz.\" However, this theoretical value is not derived from rigorous bound-state QED calculations but rather from a simple 1/n³ scaling of the measured 1S HFS, which neglects state-specific QED corrections that differ between n=1 and n=2 levels.\n\n\"The value was estimated by taking the most precise 1S HFS measurement in muonium [12] and dividing it by a factor of 2³. The uncertainty was estimated by calculating the QED D₂₁ difference [35].\"\nThis footnote in Table I reveals that the theoretical 2S HFS value is derived by scaling the experimental 1S HFS measurement of 4463.302765(53) MHz ([Liu et al., Phys. Rev. Lett. 82, 711 (1999)][2]) by 1/8, yielding ~557.9 MHz. While the 1/n³ scaling is the leading-order behavior for hydrogen-like atoms, it neglects state-specific QED corrections. The D₂₁ correction mentioned represents only one component of the difference between 1S and 2S hyperfine structure corrections. Modern QED calculations of hyperfine structure include terms such as higher-order binding corrections, radiative-recoil corrections, and state-dependent nuclear structure effects. For a first measurement claiming to determine \"for the first time the 2S hyperfine splitting in Muonium,\" a comparison to a rigorous QED calculation would strengthen the scientific significance of the result.\n\"Theoretical value HFS (*): 557.9, <0.1\"\nThe presentation of this scaled value as a \"Theoretical value\" in Table I alongside the rigorous theoretical Lamb shift value of 1047.498(0.001) MHz (from Janka, Ohayon, and Crivelli [23]) creates a misleading impression of equivalent theoretical rigor. The Lamb shift theoretical value cited is based on comprehensive QED calculations, while the 2S HFS \"theoretical value\" is an experimental value divided by eight with an uncertainty estimate from a specific correction term. The paper would benefit from either citing proper QED calculations for the 2S HFS or clearly distinguishing the nature of these two theoretical comparisons.\n* Quote (from [Karshenboim, Physics Reports 422, 1 (2005)][3]): \"The hyperfine interval in muonium has attracted a lot of attention because of the possibility of high-precision measurements... The theoretical uncertainty is mainly due to unknown higher-order contributions.\"\nThis review article on precision physics of simple atoms emphasizes that hyperfine structure calculations require careful treatment of multiple QED corrections. The scaling approach used in the paper under review, while providing a reasonable estimate, does not capture the full complexity of state-dependent QED effects that affect the 2S HFS differently from the 1S HFS.\n\nReferences:\n[2] W. Liu et al., \"High precision measurements of the ground state hyperfine structure interval of muonium and of the muon magnetic moment,\" [Phys. Rev. Lett. 82, 711 (1999)](https://journals.aps.org/prl/abstract/10.1103/PhysRevLett.82.711)\n[3] S. G. Karshenboim, \"Precision physics of simple atoms: QED tests, nuclear structure and fundamental constants,\" [Physics Reports 422, 1 (2005)](https://www.sciencedirect.com/science/article/pii/S0370157305003625)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Claude|3", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "The paper reports a detected 3S/2S ratio of 0.29(7) after correcting for decay during transit, which is lower than the estimate of 0.44(4) derived from hydrogen measurements. This ~2σ discrepancy is not explained, and the possibility that the observed 3S signal might be partially due to other systematic effects rather than purely 3S population is not fully explored.\n\n\"The effectively detected amount of 3S/2S created at the foil is 0.29(7). This agrees with the estimations done by C. Fry [36] of 0.36 and is slightly lower than the estimate of 0.44(4) from a combination of hydrogen population measurements [28, 29].\"\nThe paper describes the discrepancy with the hydrogen-based estimate of 0.44(4) as \"slightly lower,\" but a comparison of 0.29(7) to 0.44(4) yields a difference of 0.15, which represents approximately 1.9 standard deviations when combining the uncertainties in quadrature. While not definitive, this tension warrants discussion. Possible explanations could include: (1) differences in charge-exchange dynamics between hydrogen and muonium formation, (2) systematic effects in the detection or fit that could mimic 3S contributions, or (3) energy-dependent formation probabilities. The agreement with Fry's estimate of 0.36 is better, but the origin of the discrepancy with the more recent hydrogen measurements is left unexplained.\n\"An additional uncertainty in the estimated 3S/2S ratio could arise from the assumption that the detection efficiency of Lyα and Lyβ is similar. In fact, the efficiency depends on a number of factors, which make an accurate determination of its wavelength-dependency challenging.\"\nThis acknowledgment that the Lyα (121.5 nm) versus Lyβ (102.5 nm) detection efficiency difference is unknown but potentially significant affects not only the 3S/2S ratio extraction but also the overall lineshape fit. Since the 3S contribution is extracted from lineshape fitting rather than direct spectroscopic identification, any systematic difference in detection efficiency between these wavelengths would directly impact the determination of the 3S population and potentially affect the extracted transition frequency. The paper would benefit from an estimate of how much the detection efficiency ratio would need to differ to explain the 3S/2S discrepancy, or from independent verification of the 3S identification.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Claude|4", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "The systematic uncertainty budget in Table I lists several contributions as upper bounds (e.g., \"<0.16 MHz\" for MW-Beam alignment, \"<0.07 MHz\" for MW field intensity) without providing the derivations or methods used to establish these bounds. For a precision measurement intended to guide future experiments, the methodology for estimating systematic uncertainties should be more thoroughly documented.\n\n\"MW-Beam alignment: <0.16; MW field intensity: <0.07; M velocity distribution: <0.01; AC Stark 2P₃/₂: +0.39, <0.02; 2nd-order Doppler: +0.03, <0.01; Earth's Field: <0.05; Quantum Interference: <0.04\"\nTable I presents seven systematic contributions as upper bounds, but the main text provides limited detail on how these bounds were determined. While the total systematic uncertainty is small compared to the 6.8 MHz statistical uncertainty (making detailed systematic analysis less urgent for this measurement), future precision measurements targeting the ~kHz level mentioned in the paper would require rigorous characterization of these effects. For example, the MW-beam alignment uncertainty of <0.16 MHz is the largest systematic, yet no description is provided of how the alignment was verified or how this bound was derived. Similarly, the quantum interference contribution of <0.04 MHz references established effects from hydrogen spectroscopy but does not detail the calculation for muonium.\n\"The AC Stark shift due to the coupling to the 2P₃/₂ states is calculated for the average atom to be +0.39 MHz. [...] The 2nd order Doppler shift is +0.03 MHz.\"\nWhile the AC Stark and Doppler shifts are given as specific values, the uncertainties on these shifts are again presented only as upper bounds (<0.02 and <0.01 MHz respectively). For a comprehensive error budget, the uncertainties should ideally be derived from the uncertainties in the underlying parameters (microwave power, beam velocity distribution, etc.) rather than stated as bounds without justification. This is particularly relevant because the paper envisions future measurements at the kHz level where these systematics would become dominant.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|GPT|1", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "This paper’s central frequency determination for the \\(2S_{1/2},F=0 \\rightarrow 2P_{1/2},F=1\\) transition is vulnerable to line-pulling from a substantial \\(n=3\\) population, yet the manuscript does not demonstrate an experimental suppression/cross-check (e.g., quenching-on/off, altered flight time) that would bound the model-dependence, undermining **Validity** and the robustness of the extracted **Conclusions**.\n\n\"Due to the reduced influence of other nearby transitions, the systematic uncertainties related to line-pulling would become negligible.\"\nThis sentence motivates choosing the “isolated” \\(n=2\\) hyperfine transition specifically to avoid line-pulling as a limiting systematic. That framing makes control of any residual line-pulling a make-or-break requirement for the core claim that this transition is a robust LS probe. However, the rest of the manuscript shows that an additional nearby structure (from \\(n=3\\)) actually plays a dominant role in the fitted line shape. Because the paper’s measurement uncertainty is dominated by the fit (“Fitting 6.8 MHz”), an unbounded model bias from line-pulling would directly propagate into the headline 580.6(6.8) MHz result. In precision microwave spectroscopy, “negligible line-pulling” is typically justified by showing that plausible alternative line-shape models or controlled changes to the contaminant population do not shift the line center beyond the stated uncertainty; this is not shown here. As written, the manuscript asserts negligible line-pulling as a design principle but does not substantiate it for the as-operated configuration.\n\"In our measurement, the comparably large population of 3S states distorts the line-shape and introduces line-pulling, which might seem to defeat the purpose of choosing the isolated \\(n = 2\\) transition.\"\nThis sentence concedes that the core design motivation (choosing an isolated transition) is compromised by an unexpectedly important beam component. The issue is not merely an auxiliary observation: the paper relies on a fitted line shape to infer the line center, so any distortion can bias the extracted frequency. The phrase “comparably large population” indicates that \\(n=3\\) is not a small perturbation; it is potentially co-dominant with \\(n=2\\) contributions in the observable. In such situations, the standard expectation is that the authors either (i) experimentally suppress the contaminant, or (ii) rigorously propagate model uncertainty from the contaminant amplitude/shape into the final frequency uncertainty. The manuscript mainly discusses future mitigation options, but does not provide an in-run validation that current results are not significantly shifted. This leaves the primary measurement’s systematic integrity insufficiently established.\nExact fit-table excerpt comparing fits without vs. with a 3S contribution:\n\n```html\n  <tr>\n    <td>x</td>\n    <td>7.8(8)</td>\n    <td>22.0(18)</td>\n    <td>-</td>\n    <td>-24.8(74)</td>\n    <td>6.7</td>\n  </tr>\n  <tr>\n    <td>✓</td>\n    <td>3.4(11)</td>\n    <td>25.0(19)</td>\n    <td>5.0(9)</td>\n    <td>2.3(68)</td>\n    <td>2.0</td>\n  </tr>\n```\nThese two fit variants (without vs. with a 3S contribution) imply a ~27 MHz change in the fitted frequency offset, which is several times larger than the quoted 6.8 MHz statistical fitting uncertainty for the final result. That magnitude demonstrates that the line center is highly sensitive to whether (and how) the \\(3S\\rightarrow 3P\\) component is modeled, i.e., classic line-pulling behavior. If the 3S contribution is not independently constrained, then the fitted offset can absorb modeling mismatches rather than purely reflect the physical transition frequency. A large model sensitivity is not automatically fatal, but it must be paired with either strong external constraints (e.g., known 3S fraction, validated detection efficiency ratio, measured quench dependence) or an explicit model-uncertainty term in the frequency error budget. The manuscript’s uncertainty table does not separately account for uncertainty in the 3S contribution or its detection response. Consequently, the reported agreement with theory could be partly an artifact of the chosen model family rather than a robust experimental inference.\n\"An additional uncertainty in the estimated 3S/2S ratio could arise from the assumption that the detection efficiency of Lyα and Lyβ is similar. In fact, the efficiency depends on a number of factors, which make an accurate determination of its wavelength-dependency challenging (see Ref. [37, 38]).\"\nThis explicitly identifies a key nuisance parameter—how efficiently the detector sees 3S-derived Lyβ compared to 2S-derived Lyα—as difficult to determine accurately. That uncertainty directly affects the inferred 3S fraction in the fit (through \\(B_{3S}\\)) and therefore can shift the fitted line center when 3S causes line-pulling. The manuscript acknowledges the challenge but does not quantify how much the line center would move under realistic efficiency variations, nor does it include such a variation as a systematic term in Table I. Because the “with 3S” vs “without 3S” fit already produces a multi–tens-of-MHz difference, even modest uncertainty in the modeled 3S amplitude/shape could plausibly induce non-negligible shifts relative to the 6.8 MHz quoted uncertainty. In established Lamb-shift SOF-style analyses, contaminant-state effects are typically treated with dedicated suppression checks or with conservative systematic bounds when detector response is uncertain. Here, the manuscript recognizes the vulnerability but leaves it largely unbounded for the main result.\n\"These investigations indicate that interference with a neighboring resonance, even if it is very distant, can lead to significant shifts for precision measurements.\" ([1](#ref1))\nThis literature statement captures a core reason why “small” or “distant” additional resonances cannot be dismissed in precision line-center work: they can bias extracted frequencies through interference/line-shape effects. The present manuscript reports a large \\(n=3\\) population and shows strong dependence of the fitted offset on whether that contribution is included, aligning with the broader warning articulated here. Even if the 3S resonance is not extremely close in frequency, its presence can still distort the apparent line shape in a sparse scan and shift the inferred center. The cited work also emphasizes that proper treatment often requires more complete modeling (e.g., density matrix including radiative pathways) and careful assessment of systematic uncertainties. Relative to that standard, the paper’s limited bounding of 3S-induced line pulling weakens confidence that the reported 580.6(6.8) MHz is a stable, model-independent result. This is especially critical because the paper’s own motivation for the isolated transition is precisely to avoid such biases.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|GPT|2", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "The manuscript’s extraction of the transition frequency depends heavily on simulation-driven line shapes (including power corrections) built from a two-level optical Bloch approximation and fitted to only seven frequency points, but it does not provide the validation expected for such a model-dependent inference, weakening **Conclusions** and the transparency of **Data and methodology**.\n\n\"Seven frequency points are measured in the range of 200 MHz to 800 MHz with an average power of 22.3 W.\"\nA seven-point scan is extremely sparse given that the fitted function includes multiple overlapping components (three \\(n=2\\) hyperfine-related contributions and a possible \\(n=3\\) contribution) and includes at least four fit parameters (background, scaling(s), and a global frequency offset). With sparse sampling, the inferred line center becomes more sensitive to the assumed line-shape family than to the data themselves, particularly when nuisance amplitudes are weakly constrained. In such contexts, it is standard to show robustness checks (e.g., alternative scan grids, additional points near the steepest slope, different power settings) to demonstrate that the extracted center is stable. The manuscript does not report such robustness checks for the \\(580\\) MHz scan. This matters because their own fit comparison shows substantial sensitivity to inclusion of the \\(3S\\) component, suggesting that the scan density may be insufficient to break degeneracies between offset and contaminant amplitude/shape. As a result, the reported uncertainty may understate model-driven uncertainty.\n\"The average power inside the TLs is frequency-dependent. To be able to fit a line-shape, all frequency points are corrected to the same “global” power of 22.5 W, obtaining the corrected signal \\( S_c \\).\"\nPower-dependent corrections are a known source of systematic uncertainty because the excitation probability and AC Stark-related effects depend nonlinearly on field amplitude and detuning. Here, the correction \\(C(f)\\) is itself derived from simulation, so any mismatch between simulated and actual field distributions or power calibration propagates into the corrected data points before fitting. The paper does not provide enough information (e.g., measured field maps, calibration residuals, or a sensitivity study of the correction procedure) to independently evaluate whether this step can bias the fitted line center. Because only seven points are collected, even a modest frequency-dependent correction error could distort the apparent asymmetry of the scan and shift the fitted offset. In precision SOF work, power-variation effects are typically constrained either by careful field modeling validated against measurements or by experimental strategies (e.g., measuring at multiple powers) that allow empirical cross-checks. The manuscript’s description does not show such validation for the key correction that precedes the fit.\n\"Because of the linear polarization of the field in the TLs, we can approximate our system to two levels and use the relevant optical Bloch equations [32] in the simulation.\"\nThe measured spectrum arises from hyperfine-structured atoms with multiple \\(F, m_F\\) sublevels and includes radiative decay pathways; a strict two-level reduction is therefore an approximation whose adequacy depends on the precision goal and on whether other nearby states contribute coherently or incoherently. The paper does not provide an explicit justification that this approximation is sufficient for extracting an unbiased line center in the presence of overlapping transitions and an identified \\(n=3\\) contaminant. While the uncertainty table includes “Quantum Interference < 0.04”, the manuscript does not describe how that number was computed within a two-level framework or how interference between different decay pathways was treated. Modern analyses of SOF Lamb-shift measurements emphasize that quantum-interference effects and multi-level dynamics can matter at the line-center level, motivating density-matrix modeling when precision is pushed. Given the demonstrated model sensitivity in the fits, the absence of a clear validation of the two-level reduction undermines confidence that the simulation-generated line shapes accurately capture the relevant physics. This is a methodological weakness that directly impacts the reliability of the extracted frequency.\n\"Additionally, modeling the time development of the density matrix from the time at which the atom is created to the time of detection is now possible.\" ([1](#ref1))\nThis sentence reflects a common contemporary standard in high-precision microwave spectroscopy: explicitly modeling multi-level dynamics and radiative processes using density-matrix methods rather than relying on minimal two-level approximations. The cited work motivates this not as a cosmetic improvement but as a way to capture systematic effects (including quantum-mechanical interference and detailed field geometry) that can shift line centers. In contrast, the reviewed manuscript adopts a two-level approximation and does not provide a bridge showing that omitted couplings and coherences are negligible at the MHz level for the present configuration. This gap is particularly salient because the manuscript aims at an “isolated” transition precisely to reduce subtle line-shape biases, yet then confronts a multi-component spectrum that strains the two-level simplification. Without a validation step (e.g., reproducing known hydrogen line shapes or demonstrating stability under model extensions), the heavy dependence on simplified simulation limits the credibility of the final extracted frequency. The issue is methodological and affects the strength of the conclusions drawn from the fit.\n\"Due to its smaller nuclear mass, the contributions of the higher-order recoil corrections (160 kHz level) and nucleus self-energy (40 kHz level) are enhanced for muonium compared to hydrogen...\" ([4](#ref4))\nThis theoretical context explains why the experimental program emphasizes pushing systematic uncertainties well below the MHz scale: the physics targets are at \\(\\mathcal{O}(10^5)\\) Hz. The reviewed manuscript frames the isolated transition as a path toward such precision, which in turn places a premium on having a line-shape model whose systematics can be validated and controlled. However, the present analysis already exhibits line-shape sensitivity at the tens-of-MHz level depending on inclusion of extra components, signaling that the modeling framework is not yet in a regime where kHz-level effects can be meaningfully targeted. This does not invalidate the “first measurement” claim, but it does weaken the manuscript’s implied methodological readiness for the precision frontier without additional validation experiments. The gap between the observed model sensitivity and the kHz-scale physics goals suggests that systematic control and model validation should be treated as a central result rather than deferred. In short, the analysis choices should be justified in light of the known scale of the physics effects of interest.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|GPT|3", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "The manuscript reports extracted values for the Muonium Lamb shift and the \\(2S\\) hyperfine splitting, but it omits essential derivational and data-reporting details (including the per-frequency data and the combination procedure with prior measurements), limiting independent verification and reproducibility under **Data and methodology**, and weakening confidence in the **Conclusions** about the first determination of the \\(2S\\) HFS.\n\n\"From this measurement we extract the \\( 2S_{1/2}, F=0 \\rightarrow 2P_{1/2}, F=1 \\) resonance frequency to be 580.6(68) MHz and determine the M LS to be 1045.5(68) MHz.\"\nThis reports a derived LS value but does not show, within the preprint, the explicit relation used to convert a hyperfine-resolved transition frequency into the centroid Lamb shift. In the \\(I=J=1/2\\) case, this conversion requires incorporating hyperfine shifts for the specific \\(F\\) levels and therefore depends on adopted \\(2S\\) and \\(2P\\) hyperfine splittings. The preprint does not clearly state which hyperfine splitting values (measured vs. theoretical) were used for the conversion, nor does it provide the intermediate calculation. While the numerical values are plausible, the lack of explicit derivation prevents an independent reader from checking whether the LS definition, sign conventions, and inputs match common practice. This is particularly important because the manuscript’s narrative emphasizes isolating a specific hyperfine transition to reduce systematics, so the mapping from that transition to the LS should be transparent and verifiable. Without that transparency, the LS result is not fully reproducible from the manuscript.\n\"Using our previous results of the \\( 2S_{1/2}, F=1 \\rightarrow 2P_{1/2}, F=1 \\) resonance frequency [20], we extract for the first time the 2S hyperfine splitting in Muonium to be 559.6(72) MHz.\"\nThis claim depends on combining the present measurement with a prior measurement, but the preprint does not describe the statistical procedure used for the combination (e.g., whether a joint fit was performed, how correlations are treated, and what theoretical inputs were fixed). Because both measurements are performed by the same collaboration in related apparatus configurations, correlated systematics are plausible and can materially affect the uncertainty on a derived difference like the 2S HFS. The manuscript also does not provide the underlying data points for the earlier resonance scan, so the “first time” HFS determination cannot be independently reconstructed from the preprint alone. In precision spectroscopy, derived splittings are typically accompanied by the explicit formula used and a clear accounting of correlated uncertainties. The absence of such detail makes the reported 559.6(72) MHz difficult to independently validate and therefore weakens the strength of the conclusion.\n\"* The value was estimated by taking the most precise 1S HFS measurement in muonium [12] and dividing it by a factor of \\(2^3\\). The uncertainty was estimated by calculating the QED \\(D_{21}\\) difference [35].\"\nThis footnote shows that the paper’s “theoretical value HFS (*)” is not a standalone ab initio prediction for the 2S HFS, but an estimate derived from experimental 1S HFS plus a theory-motivated correction. Presenting this as a “Theoretical value” in Table I can overstate how independently the measured 2S HFS is being validated against theory. For a first measurement claim, a clear separation between (i) experimentally inferred quantities and (ii) independent theoretical benchmarks is important to interpret “agreement with theory.” If the benchmark partially inherits the experimental 1S HFS input, the comparison is less stringent than it appears. This matters for conclusions about consistency with bound-state QED, especially if future work aims at kHz-level tests where such distinctions become critical. As written, the manuscript’s presentation risks giving a stronger impression of theory validation than is warranted by an estimated reference value.\n\"To estimate the influence of the simulation input pa-rameters on the resonance position, we scan them around their uncertainty and repeat the analysis.\" ([2](#ref2))\nThis excerpt from the authors’ prior muonium LS work exemplifies a standard reproducibility and robustness practice in simulation-driven spectroscopy: explicitly varying key inputs and repeating the full analysis to quantify induced line-center shifts. In the reviewed manuscript, multiple simulation-derived elements (power correction factors, field maps, and 3S contamination modeling) can influence the fitted offset, but the preprint does not report a comparable input-sensitivity study for the current measurement. The contrast matters because the present result already shows large fit sensitivity to inclusion of extra components, making input-parameter robustness especially important. Without providing either the data or a documented sensitivity study, independent readers cannot judge whether the stated uncertainties appropriately cover simulation/model uncertainty. Thus, the methodology disclosure in the reviewed manuscript falls short of what the field commonly reports for simulation-dominated inferences. This directly limits reproducibility and confidence in the derived LS and 2S HFS.\n\"Here, a direct measurement of the *n* = 2 Lamb shift of atomic hydrogen is presented.\" ([5](#ref5))\nThis statement highlights why “direct” Lamb-shift determinations are of broad interest: they are intended to rely on well-defined spectroscopic observables that can be independently checked and reanalyzed. For such measurements, the community expectation is that the mapping from measured transition frequencies to the reported Lamb shift (including hyperfine and other corrections) is fully specified, enabling independent reproduction from the reported inputs. The reviewed manuscript’s LS and 2S HFS values are presented without enough explicit derivational detail and without tabulation of the underlying frequency-point data beyond a single off-resonance point. As a result, the work is harder to independently verify than is typical for high-impact spectroscopy results built around “direct” determinations. This does not negate the measurement, but it weakens the reproducibility and interpretability of the derived quantities. In turn, that limits how strongly the paper can support its conclusions about first determinations and agreement with theory.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "The paper reports a fitted background parameter that is statistically inconsistent with the measured background data point, or alternatively, the reported Chi-squared value is incorrect.\n\n\"An additional data point is taken with the Scanner TL turned off. ... The data point with TL OFF is not displayed in the figure, but is included in the fit; it lies at 20.4(4) × 10^-4.\"\nThe authors explicitly state that the background measurement (TL OFF) yields a value of 20.4(4) (in units of 10^-4) and that this point is included in the fit.\n\"S_BKG ... 7.8(8) ... 3.4(11)\" (from the table in the text)\nThe table reporting the fit results lists the background parameter $S_{BKG}$ as 7.8(8) for the fit without 3S and 3.4(11) for the fit with 3S. These values differ from the measured background (20.4) by approximately 16 and 17 standard deviations, respectively.\n\"Chi^2 ... 6.7 ... 2.0\" (from the table in the text)\nThe reported Chi-squared values are 6.7 and 2.0. If the \"TL OFF\" data point (20.4) were included in the fit with a model prediction of ~3.4 or ~7.8, the contribution to Chi-squared from this single point would be huge (approx. $[(20.4-3.4)/0.4]^2 > 1000$), which contradicts the reported low Chi-squared. This implies a severe inconsistency in the data analysis or reporting.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "The claim of observing the Muonium 3S state is not supported by the statistical significance of the data.\n\n\"We also present the first observation of Muonium in the n = 3 excited state.\"\nThe authors claim to have observed the 3S state for the first time. However, in particle physics and precision spectroscopy, an \"observation\" typically requires a statistical significance of at least 5 sigma.\n\"Chi^2 ... 6.7 ... 2.0\" (from the table in the text)\nThe improvement in Chi-squared when including the 3S component is only 4.7 (from 6.7 to 2.0). For one additional degree of freedom, this corresponds to a significance of roughly 2.1 sigma. Furthermore, the Chi-squared of 6.7 for the fit *without* the 3S component (with 5 degrees of freedom) corresponds to a p-value of approximately 0.24, indicating that the null hypothesis (no 3S state) provides an acceptable fit to the data. Therefore, the data does not statistically require the presence of the 3S state, making the claim of \"observation\" an overstatement.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "The method of correcting the signal for power variations before fitting is circular and introduces unquantified systematic errors.\n\n\"To be able to fit a line-shape, all frequency points are corrected to the same 'global' power of 22.5 W, obtaining the corrected signal S_c. The applied correction is given by: S_c(f) = (S(f) - S_{BKG}) \\cdot C(f) + S_{BKG}\"\nThe authors correct the experimental data points using a factor $C(f)$ derived from the same simulation model used for the final fit. This approach modifies the data to match the model's expectations regarding power dependence, rather than fitting the raw data with a model that includes the power variation.\n\"The correction factors C(f) are extracted by simulating the scaling ratio between the excitation probabilities...\"\nThis method embeds the model assumptions into the data itself. If the simulation of the power dependence is imperfect, the \"corrected\" data will be biased towards the model, potentially masking discrepancies. Furthermore, the uncertainty in the correction factor $C(f)$ does not appear to be propagated into the error bars of the corrected signal, which would lead to an underestimation of the final uncertainties.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "The analysis relies on a simulated line shape for the 3S background without quantifying the systematic uncertainty associated with the simulation accuracy.\n\n\"The individual line-shape P^{(i)} ... is constructed by simulating the excitation probability for each initial state...\"\nThe 3S contribution is modeled using a fixed line shape derived from simulations (involving SIMION field maps and optical Bloch equations). The authors fit the *amplitude* of this contribution ($B_{3S}$) but assume the *shape* is perfectly known.\n\"In our measurement, the comparably large population of 3S states distorts the line-shape and introduces line-pulling\"\nSince the 3S resonance significantly overlaps with and pulls the 2S signal, any inaccuracy in the simulated 3S line shape (e.g., due to errors in the field map or atomic trajectories) would directly shift the extracted 2S frequency. The systematic uncertainty budget (Table I) lists \"MW field intensity\" and \"MW-Beam alignment\" but does not explicitly include an uncertainty for the *shape* of the 3S background model, which is a critical omission given the magnitude of the line-pulling effect.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Gemini|5", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "The precision of the reported measurement is significantly lower than the collaboration's previous work, undermining the claim that this transition is the \"best candidate\" for future measurements without further demonstration of improved systematics.\n\n\"From this measurement we extract the 2S_{1/2}, F=0 -> 2P_{1/2}, F=1 resonance frequency to be 580.6(68) MHz\"\nThe reported uncertainty is 6.8 MHz.\n\"Our result ... is limited by the statistical uncertainty.\"\nThe authors admit the measurement is statistically limited.\n\"Combining this result with our previous measurement [20]...\"\nThe previous measurement by the same collaboration (Ref [20]) achieved an uncertainty of 2.5 MHz. The current measurement is nearly factor of 3 less precise. While measuring a new transition is valuable, the paper argues that this transition is superior (\"best candidate\") because it is \"isolated\". However, the current result does not demonstrate this advantage in practice, as it is dominated by statistics and potentially 3S line-pulling, yielding a result that is less precise than existing data.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "My doubts are regarding the scientific contents and I will omit the „Experimental method” section. Authors have previously [20] measured 2S_1/2, F=1 -> 2P_1/2, F=1 transition frequency and determined Lamb shift. In this work, they measure 2S_1/2, F=0 -> 2P_1/2, F=1 and determine Lamb Shift with 2.5 times worse accuracy. So, from the theoretical point of view only, it is not a significant achievement. So, I would expect some explanations, what is really new here.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "What is Authors’ definition of the Lamb shift ?, this should be explicitly written somewhere, Namely it is the difference in the centroid values of 2S_1/2 and 2P_1/2 levels. This is important in a view of significant mixing between P_1/2 and P_3/2 states.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "To obtain Lamb shift, Authors most probably, subtract theoretical values for the hyperfine of 2S_1/2 and 2P_1/2. This should be explicitly written, and hyperfine values given. Later Authors determine hfs of 2S_1/2, which they do not use to get the Lamb shift. They prefer theoretical predictions much more, what is not surprising.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "The value of their measured frequency 580.6(68) MHz does not somehow coincide with the value given on Fig. (1) 583 MHz, why ?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "Authors write in Abstract: „...which might provide an explanation of the g-2 muon anomaly or Lorentz and CPT violation...”. While muon g-2 is a well established anomaly, it is not the case of Lorentz and CPT violation. I would not put them on the same footing.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "It is somewhat controversial whether the paper sufficiently conveys the novelty and significance to the broad readership of Nature Communications (Even the journal’s goal is to report on the critical advances of significance to specialists within each field). Since the text is only about 3300 words compared to the journal’s regulation of 5000 words, the reviewer believes that a more specific and detailed description of the experimental method and data analysis should be added to the text.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "This paper describes results following the n=2 Lamb shift spectroscopy of muonium reported by the group at Physical Review Letters this year (B. Ohayon et al., “Precision Measurement of the Lamb Shift in Muonium,” Phys. Rev. Lett., 128, 011802 (2022), hereinafter referred to as Oyahon2022.). It is possible that this paper could be interpreted as an independent confirmation of the results reported in Oyahon2022, in which case it is difficult to determine from this manuscript whether the level of novelty and significance required by the journal has been satisfied.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "Another minor concern is that the uncertainty notation of the measurement result is inconsistent with that of Oyahon2022. For example, the Lamb shift is shown as 1047.2(2.3)stat(1.1)syst MHz in Oyahon2022, which is correct. However, this paper notes 1047.2(25) MHz, with the decimal point in the incorrect position. This error is also found in other quantities such as 2S-HFS, so the reviewer recommends that the authors check the manuscript again. From the reviewer’s point of view, the scientific significance of the motivation and the importance of the results stated in this paper are sufficient. So the reviewer would like to see a more detailed and substantive description enhanced.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "The mention of the muon discovery and g-2 deserves an introduction rather than an abstract.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "[Introduction section] The reviewer finds the first three paragraphs somewhat essayistic, not to say unnecessary, but not deeply relevant enough to be the basis for later discussion. The reviewer suggests compressing the descriptions.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "[Introduction section] Does the precision measurement of 2S-HFS have unique significance compared to 1S-HFS? If so, it is an important feature and should be explained.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "[Introduction section] The reviewer understands that the Barker-Glover effect is part of the recoil correction, but what is the significance of being able to verify this as a test for bound-state QED?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "[Experiment section] It may be semi-obvious, but F and mF should be defined in the text.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "[Experiment section] On what basis was the microwave power in the transmission line set? Is it possible to make quantitative mentions of the uniformity of the power in the area through which the muonium passes and the stability of the power during the measurement?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_2|10", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "[Experiment section] The phrase “an electrical field of the order of 250 Vcm-1” in the fourth paragraph seems a bit odd (too specific to be “an order”). Why not simply use about 250 Vcm-1 here?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_2|11", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "[Experiment section] The reviewer recommends that Lyα and Lya be unified since they are mixed in the figures and the text.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_2|12", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "[Experiment section] If the events in region A are derived from convoy electrons or ionization products, can we distinguish them from the signal by using the difference in waveform or pulse height of the MCP signals?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_2|13", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "[Experiment section] As shown in region C, does only Lya-MCP has ringing in the analog pulse and Stop-MCP has no ringing?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_2|14", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "[Experiment section] How was the microwave power measured? If the power was picked up using an antenna, then the antenna’s frequency response must be considered. Or was the power measured with a transmitting or terminated power sensor?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_2|15", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "[Experiment section] Why is the correction factor C(f) determined by the effectively measured power even though microwave power is independent of frequency?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_2|16", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "[Experiment section] What is the origin of the frequency offset (f_offset)? Is this a source of systematic error?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_2|17", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "[Results section] Reduced chi-square = 2.0 has a different meaning depending on the degree of freedom. For example, p=0.08 is obtained for chi-square10 with 5 degrees of freedom, p=0.03 for chi-square20 with 10 degrees of freedom. To eliminate ambiguity, the reviewer recommends describing both chi-square and degrees of freedom instead of reduced chi-square.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_2|18", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "[Results section] Reduced chi-squre=2 seems to imply incompleteness of the fitting function. Are there any candidates for further corrections that should be considered?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_2|19", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "[Results section] How was the TL-off data point in the line-shape included in the fitting? What does this mean in line-shape analysis (estimation of S_BKG)?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_2|20", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "[Results section] How accurate is the assumption that Lya and Lyb have similar detection efficiency? Is it possible to discuss the degree of uncertainty, even if it is difficult to evaluate precisely?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_2|21", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "[Conclusions section] Does this comparison with the hydrogen spectroscopy results provide any new insights? If so, it would be good to be a little more specific.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_2|22", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "[Conclusions section] Is there a possibility that n=3 spectroscopy, such as 3S-3D5/2, can be performed with muonium to gain new insights that have not been obtained before? If so, it would be good to be a little more specific.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "In the introduction g-2 of muon is mentioned. It is said about a 4.2 sigma deviation from a prediction. A theoretical reference is required. It is said that the deviation is `confirmed'. It would be good to mention what result was confirmed with a reference.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "I do not completely understand the wording about 'finite size'. In a sense a muon or an electron have finite-size effects, but they are calculable. The Lamb shift is a result of the size of an electron. The problem is the nuclear structure (of nuclei heavier than a proton) or the proton structure. They are not calculable and they include the nuclear finite size and nuclear polarizability. One should rather speak about hadronic structure, hadronic effects, or effects of strong interactions etc.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "To my taste, there are too many abbreviations in general and per a sentence.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "Term 'hyperfine transition(s)' is confusing. A transition between certain [hyperfine] components of the Lamb shift is not a hyperfine transition.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "'Results' section: It is said that reduced chi^2=6.7 and 2 (for different fits). 6.7 is definitely bad and that is why the other fir was performed. But I do not understand whether 2 is OK. It would be good to say what is the number of degrees of freedom and what is the probability that reduced chi^2 for those dof is >2.0.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|7|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb7", "comment": "Paragraph below Fig. 4: A theoretical value is mentioned. Then an appropriate reference should be given there.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|8|Claude|1", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "The paper uses a relativistic P-wave Breit-Wigner function to model the signal, which is acknowledged as a simplification. For a resonance located extremely close to the D\\*+D0 threshold (δmBW = −273 ± 61 keV/c²), standard Breit-Wigner parametrizations are known to be inadequate as they do not properly account for threshold effects, coupled-channel dynamics, and the energy-dependent width behavior that is critical for near-threshold states.\n\n\"Despite its simplicity, the model serves well to quantify the existence of the Tcc+ state and to measure its properties, such as the position and the width of the resonance.\"\nThe authors themselves acknowledge the simplified nature of their signal model. While they argue it is sufficient for establishing the observation, the extracted parameters (mass and width) may not represent the true physical pole parameters of the resonance. For near-threshold states, the difference between Breit-Wigner parameters and pole parameters can be substantial, affecting the physical interpretation of the state's properties.\n\"A follow-up study [90] investigates the underlying nature of the Tcc+ state, expanding on the modelling of the signal shape and determining its physical properties.\"\nThe paper explicitly defers to a follow-up study for proper characterization of the signal. This indicates that the authors recognize the limitations of their approach. The follow-up study (published in Nature Communications, Ref. [2]) indeed uses a unitarized Breit-Wigner formalism that properly accounts for threshold effects and coupled-channel dynamics, yielding notably different parameter values (δmU = −359 ± 40 keV/c² vs. δmBW = −273 ± 61 keV/c²).\n\"Because the Breit-Wigner amplitude with a constant decay width does not include the effect of the threshold, the Breit-Wigner amplitude cannot be applied to\" near-threshold states according to general amplitude analysis principles [[1]](#citation-list).\nThis statement from the literature confirms that standard Breit-Wigner parametrizations are fundamentally inadequate for near-threshold resonances. The Flatté amplitude or more sophisticated unitarized approaches are required to properly capture the threshold physics, which the authors acknowledge by deferring detailed analysis to a follow-up publication.\n\nReferences:\n[1] K. Sone, \"General amplitude of near-threshold hadron scattering for exotic hadrons,\" Physical Review D (2025). [https://scoap3-prod-backend.s3.cern.ch/media/harvested_files/10.1103/qp1j-slqg/qp1j-slqg.pdf](https://scoap3-prod-backend.s3.cern.ch/media/harvested_files/10.1103/qp1j-slqg/qp1j-slqg.pdf)\n[2] M. Karliner and J. L. Rosner, \"The doubly charmed strange tetraquark,\" arXiv:2110.12054 (2022). [https://arxiv.org/abs/2110.12054](https://arxiv.org/abs/2110.12054)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|8|Claude|3", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "While the paper claims to observe a state \"compatible with being a Tcc+ tetraquark state,\" the analysis does not provide sufficient evidence to distinguish between a compact tetraquark configuration and a loosely bound D\\*D hadronic molecular state. The proximity of the observed mass to the D\\*+D0 threshold (δm ≈ −273 keV/c²) is equally consistent with either interpretation, yet this important theoretical question is not adequately addressed.\n\n\"In this Letter, the observation of a narrow state in the D0D0π+ mass spectrum near the D\\*+D0 mass threshold compatible with being a Tcc+ tetraquark state is reported.\"\nThe identification as a \"tetraquark\" is presented cautiously but without discussion of alternative interpretations. Given that \"Due to the closeness of their masses to known particle-pair thresholds, many of these states are likely to be hadronic molecules\" as stated in the introduction, the assignment requires more careful consideration. The extreme proximity to threshold (< 1 MeV below) is actually more characteristic of molecular states in many theoretical frameworks.\n\"The near-threshold mass together with a strikingly narrow width reveals the resonance nature of the state.\"\nWhile this statement establishes that a resonance is observed, it does not address whether the state is a compact tetraquark or a molecular configuration. The theoretical literature cited in the paper (Refs. [41-46]) discusses both possibilities for QQq̄q̄ systems, and distinguishing between them requires additional observables such as production cross-sections, decay patterns, or size-related measurements.\n\n* Quote from Ref. [[2]](#citation-list): \"The proximity of this maximum to the intersection of the two M(D\\*+) dashed straight lines is a cautionary signal of a possible kinematic enhancement.\"\nThe follow-up theoretical work by Karliner and Rosner explicitly notes that the observed signal's proximity to the kinematic crossing point raises questions about its interpretation, suggesting the need for caution in assigning a purely resonant tetraquark interpretation without additional evidence.\n\nReferences:\n[2] M. Karliner and J. L. Rosner, \"The doubly charmed strange tetraquark,\" arXiv:2110.12054 (2022). [https://arxiv.org/abs/2110.12054](https://arxiv.org/abs/2110.12054)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|8|GPT|2", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "This paper’s background-subtracted \\(D^0D^0\\pi^+\\) mass spectrum and all downstream measurements are potentially biased because the sPlot procedure is used without demonstrating that the control variable (\\(m(D^0D^0\\pi^+)\\) or its constrained variant) is uncorrelated with the discriminating variables (the two \\(D^0\\) candidate masses), which is a required condition for sPlot to yield unbiased unfolded distributions.\n\n“The procedure employs the sPlot technique [110]… Each candidate is assigned a positive weight for being signal-like or a negative weight for being background-like, with the masses of the two \\( D^0 \\) candidates as the discriminating variables. All candidates are then retained and the weights are used in the further analysis for statistical subtraction of non-D\\(^0\\) background.”\nThis specifies that the paper relies on an sPlot-weighted dataset (with negative weights) to produce the spectrum that is later fit for the T\\(_{cc}^+\\) signal. In sPlot, unbiased reconstruction of a control-variable distribution requires that the control variable be uncorrelated with the discriminating variables for each component (signal and background). Here, the discriminating variables are explicitly the two reconstructed \\(D^0\\) masses; the control variable is effectively the reconstructed \\(D^0D^0\\pi^+\\) mass (after constraints and kinematic fitting). Because the \\(D^0\\) masses enter the kinematics and the event selection (mass windows and mass constraints), correlations are plausible and must be checked rather than assumed. The manuscript does not present any quantitative validation (e.g., correlation studies, closure tests, or simulation-based bias checks) that the sPlot independence condition holds in this specific reconstruction. If the condition fails, the “statistically subtracted” spectrum can be distorted in a mass-dependent way, directly impacting both the peak shape and fitted background under the signal. Given that the signal width is at the few-hundred-keV level, even small distortions could be consequential.\n“To improve the \\(m\\) mass resolution… the mass of the D\\(^0\\)D\\(^0\\pi^+\\) combinations is calculated with the mass of each D\\(^0\\) meson constrained to the known value [35].”\nThis sentence makes the dependence between the discriminating variables (the reconstructed \\(D^0\\) masses) and the control variable (the constrained \\(D^0D^0\\pi^+\\) mass) especially delicate. A mass constraint is a non-linear transformation that uses measured track momenta and reconstructed masses to adjust the kinematics, and such constraints can induce or amplify correlations between the unconstrained \\(D^0\\) mass residuals and the final constrained composite mass. Because the sPlot weights are derived from the unconstrained \\(D^0\\) masses, any residual correlation with the constrained \\(D^0D^0\\pi^+\\) mass can bias the weighted spectrum. In practice, collaborations often demonstrate that such correlations are negligible via simulation closure tests or by validating that the sWeighted control-variable distribution matches expectations when applying the method to known resonances. No such demonstration appears in the main text, leaving a key methodological assumption implicit. This is not a cosmetic omission: it is a prerequisite for treating the shown “statistically subtracted” spectrum as an unbiased estimator. Without it, reproducibility of the peak parameters is uncertain.\n“An essential assumption for the sPlot technique to apply is that the control variable is uncorrelated with the discriminating variable.” [[3]](#ref3)\nThis is the core condition under which sPlot delivers unbiased unfolded distributions for variables not used in the fit. The paper under review does not state or test this assumption for its particular choice of discriminating variables (two \\(D^0\\) masses) and control variable (the \\(D^0D^0\\pi^+\\) mass used to observe the peak). Because the selection explicitly imposes \\(D^0\\) mass windows and uses a kinematic fit, the potential for correlation is not hypothetical. In modern particle-physics analyses, it is standard to include validation plots/correlation coefficients, or to propagate a systematic uncertainty derived from closure tests if correlations are non-negligible. Absent such checks, the sPlot-based background subtraction is not fully justified as an unbiased preprocessing step. That undermines confidence in the correctness of the reported peak shape and thus the extracted mass/width parameters.\n“If the control variable x exhibits significant correlation with the discriminating variable y, the sPlots obtained with Eq. (15) cannot be compared directly with the pure distributions of the various species. In that case, one must proceed to a Monte-Carlo simulation of the procedure to obtain the expected distributions to which the sPlots should be compared with.” [[3]](#ref3)\nThis provides a concrete remedy recommended by the sPlot authors: when correlations exist, a Monte Carlo study is required to obtain the correct expectation for comparison and to assess bias. The manuscript does not report such a correlation-aware MC study for the variable of central interest (the near-threshold \\(D^0D^0\\pi^+\\) mass spectrum). Importantly, the paper’s later fit assumes that the subtracted spectrum can be interpreted as if it were the “true” prompt \\(D^0D^0\\pi^+\\) distribution. If the control/discriminant correlation is nonzero, then the fitted background under the signal and possibly the signal yield itself can be biased. This concern is amplified by the limited signal statistics (\\(117 \\pm 16\\) events) and the extremely narrow structure, where small systematic distortions can matter. Therefore, the lack of a documented correlation check is a significant reproducibility and validity problem.\n\nReferences:\n[3] [M. Pivk, F. R. Le Diberder, “sPlot: a statistical tool to unfold data distributions” (arXiv:physics/0402083)](https://arxiv.org/pdf/physics/0402083.pdf)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|8|GPT|3", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "This paper’s conclusion that the observed structure’s near-threshold mass and narrow width “reveal” a resonance is not robust because the signal is modeled with a simplified two-body P-wave Breit–Wigner ansatz (with ad hoc decay structure) even though the extracted width is comparable to detector resolution and the system is explicitly near a hadronic threshold where Breit–Wigner parameters can become non-physical or strongly model-dependent.\n\n“The near-threshold mass together with a strikingly narrow width reveals the resonance nature of the state.”\nThis is a strong interpretive statement in the abstract: it asserts that the measured mass and width *establish* a resonance interpretation. For near-threshold structures, however, the observed peak shape can be distorted by threshold effects, coupled-channel dynamics, and kinematic cusps, and thus “narrowness” in a reconstructed spectrum does not by itself distinguish resonance poles from non-resonant enhancements. The paper’s own modeling choices (see below) acknowledge simplicity and defer deeper dynamical interpretation to a follow-up study, which is in tension with this categorical abstract-level conclusion. Moreover, the reported width is of the same order as the experimental resolution, meaning the inferred “narrow width” is obtained by deconvolution and is sensitive to the assumed resolution model and lineshape form. A resonance claim should, at minimum, be supported by demonstrating stability of the extracted parameters under physically motivated near-threshold amplitudes. Without that, the abstract overstates what the present analysis establishes.\n“The signal component is described by the convolution of the detector resolution with a resonant shape, which is modelled by a relativistic P-wave two-body Breit–Wigner function… A two-body decay structure T\\(_{cc}^+ \\to\\) AB is assumed with \\(m_A = 2m_{D^0}\\) and \\(m_B = m_{\\pi^+}\\)… Despite its simplicity, the model serves well to quantify the existence of the T\\(_{cc}^+\\) state and to measure its properties…”\nThis explicitly acknowledges that the signal lineshape is treated with a simplified two-body Breit–Wigner model and an artificial “AB” decay structure that is not the physically dominant open-charm channel (which is discussed elsewhere in the paper as \\(D^{*+}D^0\\)-related near threshold). Near-threshold hadronic systems often require coupled-channel or Flatté/effective-range-like parameterizations to connect peak shapes to pole properties, especially when one channel is opening/closing in the fit region. While a simplified model can be acceptable to *demonstrate an excess*, the paper goes beyond existence and uses the Breit–Wigner parameters to support “resonance nature” language. The quoted sentence concedes the model’s simplicity but does not quantify how that simplicity impacts the physical interpretation of the width and binding relative to threshold. In particular, the ad hoc mapping of a three-body final state to a two-body P-wave Breit–Wigner can bias the extracted \\(\\delta m_{\\mathrm{BW}}\\) and \\(\\Gamma_{\\mathrm{BW}}\\) in ways not captured by small quoted systematics. This is a major issue because the paper’s headline claims hinge on the near-threshold position and extreme narrowness.\n“The root mean square of the resolution function is around 400 keV/\\(c^2\\).”\nThe quoted resolution scale is essentially the same order as the fitted Breit–Wigner width (hundreds of keV). In this regime, the inferred natural width is a deconvolution result and is highly sensitive to the resolution model and any mismodeling of its tails. Even small mismodeling can move substantial probability mass between “resolution” and “intrinsic width,” directly impacting claims like “strikingly narrow width.” The paper reports small systematic uncertainties from resolution-model variations, but those variations are within a family of parametric shapes rather than derived from a fully data-driven calibration specific to this final state. Additionally, near-threshold dynamics can change the functional form of the intrinsic lineshape, making the concept of a single Breit–Wigner width parameter fragile. Given this sensitivity, a robust resonance interpretation typically requires showing that a physically motivated near-threshold amplitude yields a consistent pole or that the data exclude non-resonant explanations. The present paper does not provide that evidence.\n“Previous measurements have assumed a Breit–Wigner resonance shape. However… this is not well motivated due to the proximity of the D\\(^0\\)D\\(^*0\\) threshold.” [[5]](#ref5)\nThis statement (from an LHCb paper on another near-threshold exotic candidate) reflects a broadly accepted methodological point: Breit–Wigner modeling can be poorly motivated near thresholds. The T\\(_{cc}^+\\) signal here is explicitly “near the D\\(^{*+}\\)D\\(^0\\) mass threshold,” so the same caveat applies in principle. The comparison is particularly relevant because it shows LHCb itself has treated near-threshold exotic lineshapes with Flatté-inspired and analytic-structure analyses when interpreting resonance properties. In the current paper, the authors instead adopt an intentionally simplified Breit–Wigner for parameter extraction while simultaneously making strong resonance-nature statements. This mismatch between the modeling rigor typically used for threshold-adjacent states and the strength of conclusions drawn here weakens the paper’s interpretability. At minimum, the manuscript should delimit which claims are purely phenomenological (peak existence) versus which are physical (resonance pole).\n“The result highlights the importance of a proper lineshape parameterisation for a measurement of the location of the pole.” [[5]](#ref5)\nThis is directly relevant to the present work because the paper interprets the measured near-threshold peak location and narrowness as evidence of a genuine resonance. Yet the Breit–Wigner parameters reported here (\\(\\delta m_{\\mathrm{BW}}\\), \\(\\Gamma_{\\mathrm{BW}}\\)) are not pole parameters, and near-threshold distortions can make their mapping to pole properties unreliable. The cited sentence emphasizes that a physically correct parameterization is crucial specifically for pole-related statements, which the current paper implicitly gestures toward by invoking “resonance nature” and citing scattering length/effective range in the summary. Although a follow-up study is referenced, the present paper’s core narrative still leans on Breit–Wigner width and sub-threshold mass to make a qualitative physical claim. This creates a risk that readers will overinterpret the Breit–Wigner fit parameters as direct resonance properties, contrary to best practices established in the literature. Therefore, the paper’s conclusions are not as robust as claimed under the presented modeling.\n\nReferences:\n[5] [LHCb collaboration, “Study of the lineshape of the χc1(3872) state” (arXiv:2005.13419)](https://arxiv.org/pdf/2005.13419.pdf)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|8|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "The paper uses a simple relativistic P-wave Breit-Wigner function to model the $T_{cc}^+$ signal, which is insufficient for a state located extremely close to the $D^{*+} D^0$ threshold. This leads to a significant overestimation of the decay width and a bias in the mass determination.\n\n\"The signal component is described by the convolution of the detector resolution with a resonant shape, which is modelled by a relativistic P-wave two-body Breit–Wigner function modified by a Blatt–Weisskopf form factor [88,89] with a meson-radius parameter of 3.5 GeV\\(^{-1}\\). ... Despite its simplicity, the model serves well to quantify the existence of the T\\(_{cc}^+\\) state and to measure its properties, such as the position and the width of the resonance.\"\nThe authors acknowledge the simplicity of the model but claim it serves well to measure properties. However, for a state with $\\delta m \\approx -273$ keV relative to the threshold, the line shape is heavily distorted by the threshold opening and cannot be accurately described by a simple Breit-Wigner. This simplification leads to physically incorrect parameters.\n\"$\\Gamma_{BW}$ ... 410 ± 165 keV\" (from Table 1)\nThe reported width of 410 keV is likely an artifact of the resolution and the inadequate model. A subsequent detailed study by the same collaboration [1] using a unitarized model found a much smaller width ($\\approx 48$ keV), indicating that the value reported in this observation paper is overestimated by an order of magnitude.\n\"While the standard Breit-Wigner parametrization generates a Tcc+ that is too broad for current theoretical calculations to reproduce, a three-body unitarized Breit-Wigner shape reveals instead a decay width...\" [2]\nTheoretical analysis confirms that the standard Breit-Wigner parametrization yields a width that is too broad and inconsistent with more rigorous unitarized approaches, which are necessary for near-threshold states.\n\nReferences:\n[1] LHCb collaboration, \"Study of the doubly charmed tetraquark Tcc+\", Nature Communications 13, 3351 (2022). https://doi.org/10.1038/s41467-022-30206-w\n[2] M. Albaladejo, \"Subleading contributions to the decay width of the Tcc+ tetraquark\", Phys. Rev. D 105, 014007 (2022). https://journals.aps.org/prd/abstract/10.1103/PhysRevD.105.014007", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|8|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "The analysis assumes a two-body decay structure $T_{cc}^+ \\to (2D^0) + \\pi^+$ with a threshold at $2m_{D^0} + m_{\\pi^+}$, which ignores the dominant intermediate state $D^{*+} D^0$ and its associated threshold behavior in the immediate vicinity of the signal.\n\n\"A two-body decay structure T\\(_{cc}^+ \\to\\) AB is assumed with \\(m_A = 2m_{D^0}\\) and \\(m_B = m_{\\pi^+}\\), where \\(m_{\\pi^+}\\) stands for the known mass of the \\(\\pi^+\\) meson.\"\nThis assumption implies that the phase space opens at $2m_{D^0} + m_{\\pi^+}$, which is approximately 6 MeV below the $D^{*+} D^0$ threshold. Since the signal is located at the $D^{*+} D^0$ threshold ($\\delta m \\approx -273$ keV), the relevant physical threshold is $D^{*+} D^0$. By using the lower 3-body threshold, the model fails to capture the rapid variation of the phase space near the signal peak, leading to distorted line shapes.\n\"The near-threshold mass together with a strikingly narrow width reveals the resonance nature of the state.\"\nThe \"resonance nature\" and its parameters depend critically on the threshold behavior. Ignoring the $D^{*+}$ width and the correct threshold location (treating it as a simple 2-body decay to $2D^0 \\pi$) misrepresents the underlying physics of the decay, which proceeds via $T_{cc}^+ \\to D^{*+} D^0 \\to D^0 D^0 \\pi^+$.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|8|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "[Overall significance] This manuscript describes an observation of a new type hadron containing four quarks, namely cc\\bar{u}\\bar{d}, which is beyond the conventional quark model telling us only baryons and mesons. The results are original and has great impact to the particle physics field usually studying sub-atom particles. It helps complete the exotic hadron picture, which is popular and of interest in a wide community over the last two decades. Within my knowledge, I think the authors credited previous work properly, except for the tetraquark candidate observed by Belle in 2013 (Phys. Rev. Lett. 110, 252002), which should be added in the reference as well.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|8|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "[Strength of the claims] P1, 2nd para, L1: I think here it's difficult to claim \\\"all exotic hadrons decay via strong interaction\\\". A quick example will be X(3872)->gamma J/psi, which is radiative transition. Also, the decay width is from \\\"keV to a few hundred MeV\\\" is more precise", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|8|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "[Strength of the claims] P1, 2nd para, L7: should be bound -> could be bound", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|8|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "[Strength of the claims] P1, 2nd para, L9: it's better to write out which pseudoscalar and vector beauty meson here.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|8|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "[Strength of the claims] P2, 2nd para: although the authors mentioned \\\"charged conjugate decays are implied\\\", is the \\( \\bar{D^0} \\bar{D^0} \\pi^- \\) mass distribution agree with the D^0D^0\\pi^+ and also shows a same narrow peak? This should be mentioned explicitly in the text.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|8|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "[Strength of the claims] P2, 2nd para: In my understanding, the DODOpi+ events was obtained in each M(DODOpi+) mass bin, by a 2-dimensional fit to the DODO mass distribution. Then in this case, you can only perform a binned maximum likelihood fit to the M(DODOpi+) distribution. Please make it clear how a unbinned fit ongoing here.", "reviewer_type": "human", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|8|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "[Strength of the claims] P2, 3rd para, L6: In the fit to the signal, the author use a P-wave resonance, and treat other options as systematic. However, in my opinion, the D^0pi^+ system is very likely to be a virtue D*+ (which is a vector), as indicated also by D^0pi^+ events in the higher mass region. Thus, it seems S-wave resonance is the most natural parameterization method, still within the J^P=1^+ assumption.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|8|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "[Strength of the claims] P2, 3rd para, last three lines: For the background term, it seems no background contribution below the D*+D0 mass threshold, due to the product of phase space with polynomial. Why? There could be 3-body phase space events near DODOpi+ threshold.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|8|Human_2|10", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "[Strength of the claims] P2, 3rd para: the authors seem never discuss possible interference between Tcc and phase space DODOpi+ events. Potential phase space background will significantly affect your signal significance.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|8|Human_2|11", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "[Strength of the claims] P3, last line: how to avoid DO-D0bar mixing here? It's interesting to see it in the Method chapter.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|8|Human_2|12", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "[Strength of the claims] P5, last three lines: \\\"The observation... further support...\\\" seems not make sense to me. Before we found the Tbb state, we can say nothing about it.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|8|Human_2|13", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "[Strength of the claims] P6, Selection, L8: The mass window of D0 is 130 MeV, what's the D0 mass resolution here? In page 2, the authors mention the resolution is 400 keV.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|8|Human_2|14", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "[Strength of the claims] P7, 1st para, L3-4: it's not clear to me what's the aim of these requirements.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|8|Human_2|15", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "[Strength of the claims] P7, 1st para: The misidentification of the bachelor pion was not mentioned in the text.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|8|Human_2|16", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "[Strength of the claims] P7, 2nd para: the non-D^0 background level for D^0 reconstruction was not mentioned in the text. Is it high, or only a small fraction? Should the reader worry about the background level, and therein the DODO signal extraction with sPlot technique?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|8|Human_2|17", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "[Strength of the claims] P8, item 1, L1: is \\\"imperfect modelling\\\" means the difference between data and MC simulation, and then a correction factor is applied? If so, please write it our more explicitly.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|8|Human_2|18", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "[Strength of the claims] P8, item 2, last line: is it possible to parameterize the background component as the sum of phase space (2-body or 3-body) and polynomial?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|8|Human_2|19", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "[Strength of the claims] P8, 4th para: For the Tcc mass measurement, with D0 candidate constrain to its nominal mass, the most relevant momentum scale is the pion track, which should be mentioned more explicitly about its quality.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|8|Human_2|20", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "[Strength of the claims] P8, 4th & 5th para: here half of the difference is taken as systematic uncertainty, and I am wondering why should only take half. Usually the full difference with +/-1 standard deviation of the source to the nominal approach should be considered as systematic uncertainty.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|8|Human_2|21", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "[Strength of the claims] P8, last para, L1: mases -> masses", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|8|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "[Strength of the claims] The first paragraph could do with being rewritten to improve the clarity of the arguments. It is hard to follow and make out the major points.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|8|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "[Strength of the claims] Is a definition of pseudo rapidity required.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|8|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "[Strength of the claims] At the end of page 3 \\\"statistically subtracting\\\"", "reviewer_type": "human", "label": "error", "error_type": "Unstated statement", "label_origin": "expert+llm-filter"}
{"id": "prb|8|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "[Strength of the claims] The final sentence of the main part of the paper \\\"The observation of this ccud tetraquark candidate close to the D*+D0 threshold further supports the existence of a bbud tetraquark that is stable with respect to the strong and electromagnetic interactions\\\" is not required and not really supported by the work in the paper. I would just drop it.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|8|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb8", "comment": "[Strength of the claims] Page 7 \\\"all track pairs of the same charge are required to have opening angle\\\" - define what this requirement is?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|9|GPT|1", "source": "prb", "split": "test", "paper_id": "prb9", "comment": "The manuscript’s headline percent-level CP-asymmetry result depends critically on cancellations between signal and control modes and on simulation-driven fit/efficiency corrections, but it does not report the key closure/robustness tests (e.g., post-correction control-mode null results and fit-bias/charge-dependent-shape stress tests) that would be expected to rule out detector/production effects at the few 0.1% level.\n\n\"The otherwise excluded \\( \\Lambda_b^0 \\to \\Lambda_c^+ (\\to p K^- \\pi^+) \\pi^- \\) decay, which shares the same final state as the signal channel, instead comprises the control channel. The \\( CP \\) asymmetry in the \\( \\Lambda_b^0 \\to \\Lambda_c^+ \\pi^- \\) decay is expected to be negligible in the Standard Model, as it is dominated by the tree-level \\( b \\to c \\bar{u} d \\) transition, making it suitable for calibrating and cancelling nuisance asymmetries.\" \nThis establishes that the core strategy is cancellation of production/detection biases using a control mode assumed to have negligible intrinsic CP violation. For such a strategy, a standard expectation is to show a clear null/closure result after *all* corrections, demonstrating that the full pipeline does not generate a spurious asymmetry when applied to the control channel. The manuscript quotes only the *raw* yield asymmetries of the control mode (not a final corrected asymmetry) and does not present a dedicated closure statement (e.g., corrected control asymmetry consistent with zero) in the main text. Because the reported global signal A_CP ~ 2.5% is not orders of magnitude larger than typical hadron-collider nuisance asymmetries, incomplete validation of the cancellation pipeline meaningfully affects confidence in the validity of the observation. This is particularly important because the nuisance-asymmetry corrections combine multiple external calibrations and pseudoexperiment-based uncertainties, where small mismodellings can coherently bias the result.\n\"In the simultaneous fit, the same probability density function for each component is used for both baryon and antibaryon decays, with the yields allowed to differ between the two samples. The yield asymmetries obtained from the mass fits are affected by nuisance effects arising from asymmetries in the \\( b \\)-baryon production cross-section, as well as from the detection, reconstruction, and selection of final-state particles. Most of these effects cancel in the difference between the yield asymmetries of the signal and the control channels. Nevertheless, the difference in the \\( \\Lambda_b^0 \\) or final-state kinematics between the signal and control channels leads to an incomplete cancellation of nuisance asymmetries.\" \nThis passage highlights two separate, nontrivial assumptions that can generate false asymmetries: (i) the mass-model shapes are constrained to be identical for baryon and antibaryon for each component, and (ii) nuisance asymmetries are handled by a mostly cancel argument plus a residual correction. Both assumptions are plausible but are also precisely the kinds of places where collaborations typically report stability/closure checks (e.g., fit-bias studies with injected asymmetries, or allowing charge-dependent shape variations) because the target effect is only a few percent. The manuscript describes systematic variations of the mass fit model, but it does not explicitly connect these variations to a demonstrated absence of charge-dependent mass-shape biases. Likewise, it asserts incomplete cancellation due to kinematic differences, but does not show a final end-to-end check that the subtraction procedure eliminates detector-induced asymmetries in a mode expected to have zero CPV. Without these explicit closure demonstrations, readers cannot independently judge whether the claimed residual nuisance-asymmetry uncertainty fully covers the possible bias mechanisms.\n\"Production asymmetries have the same experimental signature as direct CPV effects and are potentially much larger than the CP asymmetries to be determined.\" ([[6]](#ref6))\nThis statement from an LHCb production-asymmetry measurement underscores the general experimental risk at hadron colliders: production (and correlated detector) asymmetries can mimic direct CP violation unless convincingly controlled. The present manuscript’s approach (control channel plus kinematic weighting plus additional corrections) is aligned with this accepted framework, but the burden is then on clearly reported closure tests that demonstrate the residual is negligible in practice. Because the observed CP asymmetry is itself only at the few-percent level, a small unaccounted detector/production effect at the sub-percent level could materially shift the measured significance. In other LHCb measurements, such risks are often mitigated by reporting magnet-polarity splits, control-mode post-correction nulls, or additional independent control channels; analogous explicit demonstrations are not included here. The external quote supports why the absence of these checks is a major methodological gap rather than a cosmetic omission.\n\nReferences:\n[6] [LHCb Collaboration, Measurement of the D± production asymmetry in 7 TeV pp collisions, Phys. Lett. B 718 (2013) 902–909](https://core.ac.uk/download/pdf/200208716.pdf)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|9|GPT|2", "source": "prb", "split": "test", "paper_id": "prb9", "comment": "The paper’s observation claim for the global CP asymmetry relies on a simple z-score (asymmetry divided by total uncertainty) rather than a likelihood-based hypothesis test that profiles systematic uncertainties, which is not sufficiently robust for an observation-level (5σ) statement.\n\n\"The measured \\( CP \\) asymmetry, \\( \\mathcal{A}_{CP} = (2.45 \\pm 0.46 \\pm 0.10)\\% \\), with a significance of 5.2 standard deviations, reveals a difference in behaviour between baryonic matter and antimatter.\" \nThis sentence ties the central scientific claim (first observation of CP violation in baryon decays) directly to a reported 5.2 significance. Because the claimed significance is only modestly above the canonical discovery threshold, the exact statistical procedure used to convert an asymmetry measurement into a p-value matters. In particular, the total uncertainty combines statistical and systematic components that may not be strictly Gaussian or independent (e.g., systematics derived from alternative fit models and pseudoexperiments). A z-score based on a point estimate and an aggregated uncertainty can be a useful summary, but it is not automatically equivalent to a proper hypothesis test under realistic nuisance-parameter models. Without a likelihood-based significance evaluation (or an explicit demonstration that the z-score approximation is well-calibrated here), the robustness of the observation claim is weaker than standard practice in high-stakes HEP measurements.\n\"For the global \\( \\mathcal{A}_{CP} \\), the baseline method to evaluate the significance is the \\( z \\)-score which is the \\( \\mathcal{A}_{CP} \\) absolute value divided by its total uncertainty.\" \nThis explicitly defines the significance calculation as a z-score, i.e., an approximate Gaussian test based on a single summary statistic and its uncertainty. The method assumes that the estimator distribution under the null is sufficiently normal and that the total uncertainty appropriately captures all nuisance effects in a way that maps cleanly to tail probabilities. However, the analysis pipeline includes nontrivial ingredients (sPlot weighting, external efficiency asymmetry calibrations, simulation-fixed fit parameters, and alternative-model systematics), which can induce non-Gaussian behavior or correlated uncertainties. In discovery/observation contexts, HEP convention typically prefers a profile likelihood ratio (or pseudoexperiment-calibrated test statistic) precisely to avoid miscalibrated tail probabilities. The manuscript does not provide evidence (e.g., toy-study calibration of the z-score under the full pipeline) that would justify treating the quoted 5.2 as a well-defined global p-value.\n\"We describe likelihood-based statistical tests for use in high energy physics for the discovery of new phenomena and for construction of confidence intervals on model parameters. We focus on the properties of the test procedures that allow one to account for systematic uncertainties.\" ([[1]](#ref1))\nCowan et al. emphasize likelihood-based testing as the standard route for discovery claims, particularly because it provides a principled mechanism to incorporate systematic uncertainties as nuisance parameters. The present manuscript’s reliance on a z-score does not obviously implement this framework, and therefore it is not clear that the quoted standard deviations correspond to the same calibrated discovery metric used elsewhere in HEP. This matters most when the systematic model is complex or partially simulation-driven, as in this analysis. A likelihood-ratio approach would also naturally address correlations between nuisance components and the measured asymmetry, which a simple quadrature combination may not fully capture. The external reference supports the criticism that the chosen significance procedure is not aligned with common discovery-level statistical practice.\n\nReferences:\n[1] [G. Cowan, K. Cranmer, E. Gross, O. Vitells, Asymptotic formulae for likelihood-based tests of new physics (arXiv:1007.1727)](https://arxiv.org/abs/1007.1727)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|9|GPT|3", "source": "prb", "split": "test", "paper_id": "prb9", "comment": "The paper’s physical interpretation asserts that CP symmetry should hold in the \\(\\Lambda_b^0 \\to R(p\\pi^-)R(K^-\\pi^+)\\) topology because the tree amplitude does not contribute, yet the measured asymmetry in that region is non-negligible; the manuscript does not reconcile this tension (e.g., via look-elsewhere corrected significance or demonstrating consistency with residual systematics), weakening the reliability of the interpretation.\n\n\"The \\( \\Lambda_b^0 \\to R(p\\pi^-)R(K^-\\pi^+) \\) decay involves a \\( b \\to d\\bar{d}s \\) transition, where the \\( d \\) quark forms the \\( R(p\\pi^-) \\) baryon together with \\( ud \\) quarks from the initial \\( \\Lambda_b^0 \\) baryon and the remaining \\( \\bar{d}s \\) quarks forms the \\( R(K^-\\pi^+) \\) meson. In this case, the tree amplitude does not contribute, and thus \\( CP \\) symmetry is expected to hold.\" \nThis is a strong, testable theoretical statement embedded in the manuscript’s interpretation section. When such a topology is used as a quasi-null expectation, a measured nonzero asymmetry in that region becomes an important internal consistency check of the analysis. If the measured asymmetry is compatible with zero after accounting for multiple testing and systematic uncertainties, the paper should explicitly show that consistency to avoid confusion. Conversely, if the asymmetry remains notable, the statement CP symmetry is expected to hold may be too simplified for the selected mass window (which can still contain interfering contributions or residual tree pollution). The manuscript does not provide the quantitative reconciliation needed to support its interpretive narrative.\n\"<td>\\( \\Lambda_b^0 \\to R(p\\pi^-)R(K^-\\pi^+) \\)</td>\" and \"<td>(2.7  0.8  0.1)%</td>\" \nNumerically, this corresponds to a roughly 3 deviation from zero if one uses the quoted uncertainties in the same way the manuscript uses them elsewhere (i.e., dividing by the total uncertainty). Even if the authors later argue that this is not significant after accounting for the look-elsewhere effect across multiple regions, the paper does not report the corrected p-value or corrected significance for this specific region. Because the interpretation claims CP should hold here, leaving this apparent deviation unquantified is problematic: it can either indicate residual experimental bias in that region or reflect inadequacy of the simplified topology-level argument. Either way, the absence of a clear reconciliation weakens confidence in the data interpretation. Reporting the look-elsewhere corrected significance (and/or a dedicated systematic cross-check) for this null-expected region would materially improve the robustness of the conclusions.\n\"When searching for a new resonance somewhere in a possible mass range, the significance of observing a local excess of events must take into account the probability of observing such an excess anywhere in the range. This is the so called \\\"look elsewhere effect\\\".\" ([[2]](#ref2))\nWhile Gross & Vitells discuss look-elsewhere effects for resonance searches, the underlying principle applies generally: when multiple correlated regions or selections are examined, local significances can be inflated relative to global significance. The manuscript acknowledges a look-elsewhere correction for the local \\(\\mathcal{A}_{CP}\\) measurements, but it does not provide the corrected significance values for each region, including the topology where CP is expected to hold. Given the tension between expectation and the quoted central value, readers need the globally adjusted significance (or an explicit statement that the result becomes fully compatible with zero) to interpret this check correctly. Without this, the narrative risks appearing internally inconsistent: CP should hold is stated, yet a seemingly notable asymmetry is reported in the corresponding region. The external reference supports why the paper should explicitly quantify how multiple testing affects this apparent deviation.\n\nReferences:\n[2] [E. Gross, O. Vitells, Trial factors for the look elsewhere effect in high energy physics (arXiv:1005.1891)](https://arxiv.org/abs/1005.1891)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|9|GPT|5", "source": "prb", "split": "test", "paper_id": "prb9", "comment": "The manuscript’s analysis choices (simulation-fixed fit shapes, external calibration inputs, and pseudoexperiment-based uncertainties) are not documented in enough detail, and are not accompanied by reusable released artifacts, to enable independent reproduction or reanalysis of the key result.\n\n\"The signal shape is modelled as a combination of a Gaussian and two Crystal Ball functions [49], all sharing the same peak position. The parameters of the signal function are determined from simulated events and are fixed in the fit to data, except for the Gaussian width, the average width of the Crystal Ball functions, and the peak position, which accounts for imperfections in the simulation.\" \nThis shows that the extracted yields (and thus the asymmetry) depend on simulation-derived shape parameters that are not fully floated in the data fit. For an external reader, reproducing the measurement requires access not only to the data but also to the exact simulation configuration, the derived fixed parameter values, and the fitting implementation. The manuscript does not tabulate these fixed parameters or provide a machine-readable specification of the full likelihood model, making an independent reproduction infeasible even in principle. This is not merely a documentation issue: if fixed parameters shift yields differently for baryon and antibaryon due to subtle reconstruction differences, the asymmetry can be biased. Providing the parameter values and a compact statistical model description (or a public likelihood artifact) would significantly strengthen reproducibility and facilitate scrutiny.\n\"The Durham High Energy Physics Database (HEPData) has been built up over the past four decades as a unique open-access repository for scattering data from experimental particle physics papers. It comprises data points underlying several thousand publications.\" ([[3]](#ref3))\nThis reference illustrates an established community mechanism for releasing the numerical content underlying published results in particle physics. For a paper making a historically significant first observation claim, depositing the key measurement tables (e.g., asymmetries, uncertainties, and possibly binned distributions needed for reinterpretation) in such repositories is a common and impactful practice. The manuscript does not indicate any such deposit or provide equivalent machine-readable artifacts for the measurement, which limits downstream re-use and independent cross-checking. While raw LHCb collision data may not be trivially shareable, the derived high-level results and auxiliary tables often are. The absence of an explicit artifact release therefore materially harms reproducibility under common open-science norms in HEP.\n\"CERN today launched its Open Data Portal where data from real collision events, produced by experiments at the Large Hadron Collider (LHC) will for the first time be made openly available to all.\" ([[4]](#ref4))\nThis CERN policy statement demonstrates that LHC data and accompanying tools can, in some circumstances, be released openly and in a reusable form. While not all analyses can be reproduced from open data today, the existence of such infrastructure raises the bar for transparency around what is (or is not) being shared for a particular result. The manuscript provides no data/code availability statement and no pointers to reusable analysis materials, leaving readers unable to assess what is needed to reproduce the published asymmetry. Even if full reproduction is restricted to the collaboration, providing analysis-level outputs (tables, simplified likelihoods, or open code for the statistical treatment) would enable partial independent validation. The external quote supports the expectation that major LHC results should, where feasible, provide clearer pathways for data and tool sharing.\n\nReferences:\n[3] [E. Maguire, L. Heinrich, G. Watt, HEPData: a repository for high energy physics data (arXiv:1704.05473)](https://arxiv.org/pdf/1704.05473)\n[4] [CERN, CERN makes public first data of LHC experiments (Open Data Portal announcement)](https://home.cern/news/news/accelerators/cern-makes-public-first-data-lhc-experiments)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|9|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb9", "comment": "The paper fails to discuss or quantify the potential systematic bias arising from the polarization of the $\\Lambda_b^0$ baryon, which can induce artificial asymmetries in the detection efficiency.\n\n\"The initial $pp$ collision is a two-baryon system, which produces slightly more $\\Lambda_b^0$ baryons than $\\overline{\\Lambda}_b^0$ baryons, resulting in an asymmetry that depends on their rapidity $y$ and their $p_T$ [34].\"\nThe authors acknowledge production asymmetry in terms of yield but neglect the polarization of the produced baryons. In $pp$ collisions, $\\Lambda_b^0$ baryons can be produced with a non-zero transverse polarization.\n\"Subsequently, the detection asymmetry for each final-state particle as a function of kinematics is averaged over the kinematic distribution in both the signal and control channels.\"\nThe efficiency correction relies on reweighting kinematic distributions ($p_T, y$) and using detection asymmetry maps. However, if the $\\Lambda_b^0$ is polarized, the angular distribution of its decay products is non-uniform and depends on the polarization vector. Since the detector acceptance is also non-uniform, a coupling between polarization and acceptance arises. If the polarization of $\\Lambda_b^0$ and $\\overline{\\Lambda}_b^0$ differs (or if the detector response to their decay angular distributions differs), this can create a spurious asymmetry that is not corrected by simple $p_T-y$ reweighting or single-particle efficiency maps.\n\"Measurements of the $\\Lambda_b^0 \\to J/\\psi \\Lambda$ decay amplitudes and the $\\Lambda_b^0$ polarisation in $pp$ collisions at $\\sqrt{s} = 7$ TeV [hyperlinked citation]\"\nPrevious measurements by LHCb [2] have investigated $\\Lambda_b^0$ polarization. While found to be small at 7 TeV, it may be non-negligible at the higher energies (13 TeV) included in this analysis (Run 2). The absence of any discussion or systematic uncertainty assignment regarding polarization effects undermines the robustness of the \"first observation\" claim.\n\nReferences:\n[2] LHCb collaboration, R. Aaij et al., Measurements of the $\\Lambda_b^0 \\to J/\\psi \\Lambda$ decay amplitudes and the $\\Lambda_b^0$ polarisation in $pp$ collisions at $\\sqrt{s} = 7$ TeV, Phys. Lett. B 724 (2013) 27.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|9|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb9", "comment": "The paper attributes the observed CP violation to specific intermediate resonances (e.g., $R(p\\pi^+\\pi^-)$) without performing a full amplitude analysis to disentangle interference effects.\n\n\"This discovery strongly suggests that specific intermediate resonances play a key role in generating $CP$ violation in $\\Lambda_b^0$ decays.\"\nThe authors claim that specific resonances are responsible for the CP violation based on observing asymmetry in a specific mass region. However, in four-body decays, interference between different resonant and non-resonant amplitudes is complex. A significant asymmetry in a mass projection could result from the interference of a resonance with a broad non-resonant component or another resonance, rather than the resonance itself.\n\"In particular, the $CP$ asymmetry is found to be most pronounced in the region dominated by the resonant decays $\\Lambda_b^0 \\to R(p\\pi^+\\pi^-)K^-$\"\nIdentifying a region \"dominated\" by a resonance does not isolate the CP violating phase to that resonance. Without a full amplitude analysis (as performed in similar $B$-meson studies cited in the paper, e.g., [25, 27]), the conclusion that specific resonances \"play a key role\" is qualitative and potentially misleading. The observed local asymmetry confirms CP violation exists in that phase space region, but the physical mechanism (specific resonance vs. interference) remains ambiguous.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|9|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb9", "comment": "The manuscript is generally very clear and complete, but it gives the impression of being written in 2 separate parts, with many useful experimental and analysis details given only in the second part. It might be useful to the reader to include, at some point e.g. around the beginning of page 2, a sentence saying that the detailed experimental methods are described later in the text (line 269). Another reference to the later Methods sections could be added to the end of the sentence starting in line 82;", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|9|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb9", "comment": "Line 11: perhaps “dominance of matter” would be more clear and accurate than “persistence of matter”;", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|9|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb9", "comment": "The non-expert reader may be surprised that the Feynman diagrams in Figure 1 do not include the pion pair constituents in an obvious way. I would suggest trying a more complete description of the decay by augmenting the sentence “where the quarks eventually form…” in the figure caption;", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|9|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb9", "comment": "Line 299 and later: for clarity I would advise the use of “collision data” or some equivalent term instead of “data” (simulation data are data, after all);", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|9|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb9", "comment": "Line 312: I believe this is the first use of p_T; please define it as transverse momentum;", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|9|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb9", "comment": "Line 366 and following: I assume that the fits mentioned are performed separately for both run periods. Is this correct? Are the fit results (distribution widths, for example) comparable, and are they consistent with simulation?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|9|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb9", "comment": "I feel it is not clearly spelled out what is actually measured: It is said that the CP asymmetry in the decay Lambda_b to p K- pi+ pi- is studied. However, you do not measure the direct decay as intermediate resonant contributions are included (and probably are even the dominant contribution to the CP asymmetry). On the other hand charmed resonances are vetoed (this is the control channel). What you actually measure becomes clear only after looking at the Feyman diagrams in Fig. 1.\\n\\nSo, I would write in the abstract and in the introduction that you study the CP asymmetry in Lambda_b decays to p K- pi+ pi- corresponding to b -> u or b -> s quark level transitions.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|9|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb9", "comment": "Fig. 1\\n\\nI understand that also b -> s s s-bar can contribute when f0(980) -> pi+ pi- is formed. So, why is this not shown in the second Feynman diagram?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|9|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb9", "comment": "No attempt is made to correct the yields for finite trigger and reconstruction efficiency. I’m ready to believe that most of the effect cancels in the ratio and is removed when subtracting the nuisance asymmetry. But shouldn’t at least the difference in nuisance asymmetries between signal and control channel have some model-dependence based on which resonances actually contribute to the signal and to which extent? I would appreciate your comments on this point.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|9|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb9", "comment": "The CP asymmetry is claimed to be 5.2 sigma which seems to be simply the central value divided by the quadratic sum of statistical and systematic errors. Has it been confirmed that errors are Gaussian to justify this approach? The systematic error is sub-dominant but if it would be, e.g., flat would this change anything to the 5 sigma claim?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|9|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb9", "comment": "I think it would be good to spell out at least a few of the hadronic resonances you have in mind. This would allow the Reader to better understand the mass region selections in Table 1.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|9|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb9", "comment": "Please spell out which charm resonances you veto: Is it only Lambda_c -> p K- pi+ and D0 -> K- pi+ or are there also other modes (like D+ -> K- pi+ pi-).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|9|Human_3|7", "source": "prb", "split": "test", "paper_id": "prb9", "comment": "Can you please comment on the compatibility of the run 1 and 2 datasets? For the signal mode, the yield asymmetries differ by 1.5 sigma while for the control mode the difference is only 0.4 sigma. How statistically likely is this outcome?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|9|Human_3|8", "source": "prb", "split": "test", "paper_id": "prb9", "comment": "Is the mass fit using the same widths for Lambda_b and Lambda_b-bar? I understand that the widths are determined from data but are they constrained to be identical for particle and anti-particle? I would not be obvious to me that this must be the case.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|9|Human_3|9", "source": "prb", "split": "test", "paper_id": "prb9", "comment": "It is explained how the shapes of the different backgrounds are modeled but nothing is said about their normalization. Are the background yields freely floated in the mass fit or are they constrained somehow?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|9|Human_3|10", "source": "prb", "split": "test", "paper_id": "prb9", "comment": "Extended Data Table 1\\n\\nPID asymmetry difference error: It is 0.141% for run 1 but only 0.002% for run 2. How can you explain such a large difference?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|9|Human_3|11", "source": "prb", "split": "test", "paper_id": "prb9", "comment": "Extended Data Table 2\\n\\nIt is odd that the mass fit systematics are larger for run 2 (0.067%) than for run 1 (0.044%). Otherwise uncertainties have always been smaller for run 2 (due to the larger integrated luminosity). Can you please comment.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|10|Claude|1", "source": "prb", "split": "test", "paper_id": "prb10", "comment": "The paper claims an \"unexpected dependence of the production rate on track multiplicity\" comparing T_cc+ production to χ_c1(3872), but does not provide a quantitative statistical test to establish the significance of this difference or characterize how unexpected the observation is.\n\n\"Unlike the prompt production of the χc1(3872) state, no suppression of the Tcc+ state production at high track multiplicities is observed relative to the low-mass D0D̄0 pairs. The observed similarity with the multiplicity distribution for the low-mass D0D0 production process, that is presumably double-parton-scattering dominated, is unexpected.\"\nThis statement constitutes a key physics conclusion about the nature of T_cc+ production. However, the paper does not quantify the statistical significance of the difference between T_cc+ multiplicity dependence and that of χ_c1(3872). The prior LHCb publication on χ_c1(3872) multiplicity dependence (Phys. Rev. Lett. 126, 092001 (2021)) used the ratio of χ_c1(3872) to ψ(2S) cross-sections as a function of multiplicity and performed fits to quantify the dependence. In contrast, this paper presents only a visual comparison in Figure 7 without comparable quantitative analysis. Given that this observation is highlighted as a major finding (\"unexpected\"), the lack of a formal statistical comparison undermines the strength of this conclusion.\n\n* Quote from [LHCb, Phys. Rev. Lett. 126, 092001 (2021)](https://arxiv.org/abs/2009.06619): \"The ratio of χc1(3872) to ψ(2S) cross-sections for promptly produced particles is also found to decrease with multiplicity, while no significant dependence on multiplicity is observed for the equivalent ratio of particles produced away from the collision vertex in b-hadron decays.\"\nThe previous LHCb study on χ_c1(3872) employed a ratio-based analysis that normalized out common production effects and provided quantitative measurements of the multiplicity dependence. In the T_cc+ paper under review, Figure 7 shows T_cc+ yields versus D0D̄0 and D0D0 yields in multiplicity bins, but without a comparable ratio analysis or χ² test for the hypothesis that T_cc+ has the same multiplicity dependence as D0D0 pairs. The limited statistics (186 events total) contribute to large uncertainties in each multiplicity bin, making visual inspection insufficient to draw firm conclusions about production mechanisms.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|10|Claude|2", "source": "prb", "split": "test", "paper_id": "prb10", "comment": "The compositeness Z is derived from the effective range expansion, but the effective range r itself is only constrained as a one-sided upper limit (-r < 11.9 fm at 90% CL), making the compositeness interpretation more model-dependent than the presentation suggests.\n\n\"Z < 0.52 (0.58) at 90 (95)% CL.\"\nThe compositeness Z < 0.52 is presented as a meaningful constraint on the molecular nature of T_cc+. However, this bound is directly tied to the effective range parameter r, which is only constrained as an upper limit. The compositeness formula from the effective range expansion, as noted in the literature (e.g., Weinberg's relations), requires knowledge of both the scattering length a and effective range r. When r is poorly constrained, the compositeness Z inherits significant model dependence. The bound Z < 0.52 essentially reflects the saturation behavior of the |g| parameter rather than a direct measurement of the compositeness.\n\"−r < 11.9 (16.9) fm at 90 (95)% CL.\"\nThe effective range is constrained only as an upper limit, meaning the data are consistent with r → 0 up to the quoted bound. This is a consequence of the |g| parameter being in the saturated regime (large |g|), where the fit cannot distinguish between different values of |g| (and hence r). The compositeness interpretation using Weinberg's relation Z = 1 - |a/(a - r/2)|² requires precise knowledge of both a and r. With r only bounded from above, the systematic uncertainty on the compositeness interpretation is substantial and should be more prominently acknowledged in the conclusions.\n\n* Quote from [Matuschek et al., Eur. Phys. J. A 57 (2021) 101](https://arxiv.org/abs/2007.05329): \"The compositeness can be expressed as a function of the model parameters and the binding energy.\"\nRecent theoretical work has emphasized that compositeness interpretations near threshold depend sensitively on both scattering length and effective range. When the effective range is poorly determined, as in this analysis, the mapping between measured parameters and compositeness becomes ambiguous. The bound Z < 0.52 constrains the state to have at least ~48% non-molecular component, but this conclusion should be qualified by noting that r itself is not measured, only bounded.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|10|Claude|3", "source": "prb", "split": "test", "paper_id": "prb10", "comment": "The key parameter |g| governing the T_cc+ → D*D coupling saturates at large values in the likelihood fit, meaning only a lower bound can be set, which limits the extraction of the natural width and other derived quantities.\n\n\"The likelihood profile for the parameter |g| is shown in Fig. 2, where one can see a plateau at large values.\"\nThe likelihood profile shows that for |g| > ~10 GeV, the likelihood becomes flat (saturated), meaning the data cannot distinguish between different large values of |g|. This saturation implies the analysis operates in the \"scattering-length approximation\" regime where the natural line shape is dominated by threshold effects rather than the intrinsic width. While this is appropriately acknowledged, it means that quantities depending on |g| (such as the natural width Γ and the effective range r) cannot be directly measured but only bounded.\n\"The lower limits on the |g| parameter of |g| > 7.7 (6.2) GeV at 90 (95)% confidence level (CL) are obtained as the values where the difference in the negative log-likelihood −Δ log L is equal to 1.35 and 1.92, respectively.\"\nOnly lower limits on |g| can be extracted, not a measurement. This limitation propagates to all derived quantities that depend on |g|. In Table 2, |g| is fixed to 3 × 10⁴ GeV for the default fit, which is in the saturated regime. The pole width Γ_pole = 48 ± 2⁺⁰₋₁₄ keV has a large asymmetric systematic uncertainty from the unknown |g| value, reflecting this fundamental limitation. The paper correctly reports these as limits but the implications for physical interpretation (particularly about the compact vs. molecular nature debate) should be more cautiously stated.\n\"In this regime of large |g|, the F^U signal profile exhibits a scaling property similar to the Flatté function.\"\nThis scaling property means that the line shape in the saturated regime is determined primarily by the D* width (~60 keV) rather than the intrinsic T_cc+ properties. While this is a valid physical regime for near-threshold states, it means the analysis cannot distinguish between a loosely-bound molecular state (large |g|) and states with intermediate |g| values. The physical conclusions about T_cc+ being \"exotic\" and having large spatial extent are robust, but finer details about its internal structure remain inaccessible with current statistics.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|10|GPT|1", "source": "prb", "split": "test", "paper_id": "prb10", "comment": "This paper draws overly strong, model-dependent inferences about the internal structure of the observed near-threshold state (e.g., “compositeness” and an implied large spatial size) and presents them as quasi-direct physical observables, which weakens the validity of the structure interpretation based on the low-energy parameters and the Weinberg criterion.\n\n“The Weinberg compositeness criterion [135,136] makes use of the relation between the scattering length and the effective range to construct the compositeness variable \\( Z \\),\n\n\\[\nZ = 1 - \\sqrt{\\frac{1}{1 + 2|r/\\Re a|}} ,\n\\]\n\nfor which \\( Z = 1 \\) corresponds to a compact state that does not interact with the continuum, while \\( Z = 0 \\) indicates a composite state formed by compound interaction.”\nThis passage assigns a near-binary physical interpretation (“compact” versus “composite”) to \\(Z\\) as computed from an effective-range-based relation, but the state studied here is not a stable, single-channel bound state: it is produced and observed through an open three-body channel \\(D^0D^0\\pi^+\\) and has an explicitly complex scattering length later in the text. In such settings, standard compositeness constructions are known to become subtle because the relevant amplitudes have inelasticities, unstable constituents, and analytic-structure complications beyond a single-channel effective range expansion. The paper does not clearly justify why the stated mapping of \\(Z\\in[0,1]\\) to “compact/composite” remains reliable under these conditions rather than being a convention within a specific amplitude model. This matters because the manuscript presents \\(Z\\) as a key discriminator of the state’s nature rather than as a model-dependent diagnostic. The result is that the structural conclusion is less robust than the prose implies, even if the underlying fit to the mass spectrum is sound.\n“From the low-energy limit of the amplitude, the estimates for the scattering length \\( a \\), effective range \\( r \\), and the compositeness, \\( Z \\), are obtained”\nThe quoted sentence frames \\(a\\), \\(r\\), and \\(Z\\) as “obtained” from the amplitude in a way that reads as if they are direct experimental outputs, but in practice they are derived quantities that depend on how the amplitude is defined, matched, and extrapolated to the low-energy limit. The text elsewhere indicates that key model ingredients (e.g., the treatment of thresholds and the unitarised three-body amplitude) are required to perform this extraction, meaning the mapping from fitted parameters to \\(a\\), \\(r\\), \\(Z\\) is not unique across plausible amplitude parameterizations. For near-threshold systems, small differences in the analytic continuation or inclusion of coupled-channel/three-body effects can shift the low-energy parameters materially. Without a more explicit demonstration of robustness across model variants specifically for \\(Z\\) (not just the peak position), the derived structural interpretation remains fragile. This is significant because the manuscript elevates these derived parameters to central physics conclusions.\n“The pole position, scattering length, effective range and compositeness form a complete set of experimental observables related to the \\( T_{cc}^{++} \\to D^0 \\overline{D}^0 \\pi^+ \\) reaction amplitude, which is vital for inferring the nature of the \\( T_{cc}^{++} \\) tetraquark.”\nCalling compositeness (and even the effective range in this context) an “experimental observable” overstates its status: the pole position is comparatively close to a model-independent characterization, but \\(a\\), \\(r\\), and especially \\(Z\\) depend on the chosen low-energy expansion and on how multi-channel and three-body effects are treated. The paper itself highlights that the amplitude involves multiple branch points and thresholds, which is precisely where the minimal effective-range picture can be least reliable without additional checks. Presenting this set as “complete” suggests that no additional dynamical assumptions enter the inference, yet the derived \\(Z\\) is explicitly tied to \\(|g|\\) behaviour and matching assumptions described in Methods. This risks giving readers the impression that the compositeness conclusion is as experimentally grounded as the mass measurement, which is not supported by the analysis as written. As a result, the strength of the claimed “information about the nature” is overstated.\n“However, theoretical studies have shown that any state with a finite eigenenergy can in principle take an arbitrary value of the compositeness.” ([3](#ref3))\nThis sentence from the literature directly challenges the idea that compositeness is automatically a sharply diagnostic quantity for near-threshold states with finite binding/width: it emphasizes that \\(X\\) (and thus \\(Z\\)) can be made to vary widely depending on dynamics and definitions when the state is not at the strict threshold limit. In the reviewed paper, the resonance is close to threshold but not in the idealized limit where universal relations become strictly model independent, and it is affected by open decay channels. Therefore, reporting an upper limit on \\(Z\\) is not, by itself, a definitive classifier of “compactness” unless the analysis demonstrates that the extracted \\(Z\\) is stable under reasonable variations of the amplitude framework. The paper does not present such a stability study for \\(Z\\), beyond noting its dependence on \\(|g|\\). This undermines the reliability of the structural conclusion as presented. The quoted literature thus supports that the manuscript’s interpretive leap is larger than is commonly warranted.\n“However, as noticed in Ref. [11,12,13], the effective-range formulae are not the most general ones even in the small-momenta limit. The scattering amplitude, as a func-tion of energy, can have a zero and, if this zero is situated in the near-threshold region, the effective-range expansion would fail.” ([4](#ref4))\nThe paper under review relies on an effective-range-style low-energy expansion to interpret \\(a\\), \\(r\\), and \\(Z\\), but this quoted result highlights a concrete failure mode: near-threshold zeros can invalidate the effective-range expansion even at low momentum. The reviewed manuscript does not clearly demonstrate that its extracted amplitude is free of such complications (or that their impact is negligible) over the region used to infer \\(a\\), \\(r\\), and \\(Z\\). In near-threshold hadron spectroscopy, such analytic-structure effects are not purely academic because coupled-channel dynamics and nearby thresholds are common. Thus, without an explicit robustness check, the effective-range-based compositeness inference is potentially sensitive to precisely the kind of non-generic behaviour described here. This does not invalidate the mass-spectrum signal, but it does materially weaken claims that \\(Z\\) robustly reveals the state’s internal structure.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|10|GPT|2", "source": "prb", "split": "test", "paper_id": "prb10", "comment": "This paper applies Wilks’ theorem and fixed \\(-\\Delta\\log\\mathcal{L}\\) thresholds to obtain significances and confidence limits in settings where regularity conditions are plausibly violated (e.g., hypotheses on parameter boundaries and an effectively non-identifiable coupling with a likelihood plateau), which threatens the validity of the quoted significances and limits.\n\n“The statistical significances of the observed \\( T_{cc}^+ \\to D^0 D^0 \\pi^+ \\) signal and for the \\( \\delta m_U < 0 \\) hypothesis are determined using Wilks’ theorem to be 22 and 9 standard deviations, respectively.”\nThe manuscript reports very high Gaussian-equivalent significances based explicitly on Wilks’ theorem, but Wilks’ theorem requires regularity conditions that can fail when testing hypotheses on boundaries or with nonstandard likelihood shapes. The “\\(\\delta m_U < 0\\)” statement indicates a one-sided/boundary-type hypothesis test (since the sign of \\(\\delta m_U\\) is physically meaningful as binding/unbinding), which is precisely a regime where the asymptotic \\(\\chi^2\\) calibration can change. In near-threshold resonance models, parameters can also be weakly identified or constrained by physical boundaries, further challenging Wilks-style calibrations. Although 22\\(\\sigma\\) is so large that the qualitative existence of a signal is unlikely to hinge on asymptotic details, the 9\\(\\sigma\\) claim for \\(\\delta m_U < 0\\) is more sensitive to the test-statistic calibration. The paper does not provide a toy-MC or alternative asymptotic treatment tailored to boundary cases, leaving the numerical interpretation of these significances insufficiently supported.\n“In this regime of large \\( |g| \\), the \\( \\mathfrak{F}^U \\) signal profile exhibits a scaling property similar to the Flatté function [104,107,108]. The parameter \\( |g| \\) effectively decouples from the fit model, and the model resembles the scattering-length approximation [94]. The likelihood profile for the parameter \\( |g| \\) is shown in Fig. 2, where one can see a plateau at large values.”\nAn explicit likelihood plateau indicates that \\(|g|\\) is not well identified by the data over a wide region, meaning the usual quadratic approximation that underpins many asymptotic likelihood results can fail. When a parameter effectively “decouples,” likelihood-based intervals can become highly sensitive to the chosen parameterization, boundary handling, and profiling procedure. In such cases, interpreting \\(-\\Delta\\log\\mathcal{L}\\) differences as standard \\(\\chi^2\\) thresholds is not automatically justified. The paper acknowledges the plateau qualitatively but still proceeds to report sharp one-sided CL bounds on \\(|g|\\). Without demonstrating coverage (e.g., via pseudoexperiments tailored to the \\(|g|\\) plateau) the numerical confidence levels can be miscalibrated. This is a substantive statistical issue because \\(|g|\\) feeds directly into derived physics quantities later emphasized.\n“The lower limits on the \\( |g| \\) parameter of \\( |g| > 7.7 \\) (6.2) GeV at 90 (95)% confidence level (CL) are obtained as the values where the difference in the negative log-likelihood \\( -\\Delta \\log \\mathcal{L} \\) is equal to 1.35 and 1.92, respectively.”\nThe stated mapping from \\(-\\Delta\\log\\mathcal{L}\\) to CL thresholds implicitly assumes a regular \\(\\chi^2\\) calibration for a one-parameter profile likelihood. But the paper itself describes a likelihood shape with a plateau and physical regimes where the signal becomes too narrow to resolve, both of which can break the assumptions behind that calibration. Additionally, one-sided bounds for parameters that are effectively bounded or weakly identified often require modified asymptotic distributions or explicit toy-MC calibration to ensure correct coverage. The text does not specify such a calibration for \\(|g|\\), nor does it show that the chosen \\(-\\Delta\\log\\mathcal{L}\\) thresholds yield nominal 90/95% coverage in this problem. Since \\(|g|\\) influences the effective range and compositeness discussion, any miscalibration propagates into key interpretive outputs. This makes the reported confidence limits potentially unreliable as quoted.\n“In these and other settings that involve testing a hypothesis that is on the boundary of the parameter space, {\\it contrary to common practice, the nominal \\(\\chi^2\\) distribution for the LRT or the \\(F\\) distribution for the \\(F\\) test should not be used}.” ([1](#ref1))\nThis literature statement summarizes a widely recognized statistical caveat: boundary hypotheses invalidate naive Wilks-style \\(\\chi^2\\) calibrations, even asymptotically, in common scientific testing scenarios. The reviewed paper performs at least one boundary-style hypothesis test (\\(\\delta m_U < 0\\)) and relies on profile-likelihood thresholds for one-sided limits, both of which can fall under boundary/irregular conditions. Therefore, the manuscript’s explicit reliance on Wilks’ theorem without a boundary-aware correction or toy-MC validation is in tension with established statistical guidance. While experimental HEP often uses asymptotic approximations, standard practice in such boundary cases is to either use modified asymptotics (mixture distributions) or validate with pseudoexperiments. The absence of such a calibration step weakens confidence in the quoted numerical significances/CLs as exact frequentist statements. The quote thus supports that the paper’s statistical procedure may be misapplied in this setting.\n“In many analyses, the contribution of the signal process to the mean number of events is assumed to be non-negative. This condition effectively implies that any physical estimator for \\(\\mu\\) must be non-negative.” ([2](#ref2))\nThis sentence captures a canonical reason why Wilks’ theorem often needs modification in discovery-style tests: physical signal strengths are frequently constrained to be non-negative, creating a boundary at \\(\\mu=0\\). The reviewed paper’s use of Wilks’ theorem for discovery-like significances and one-sided hypotheses is analogous in that it involves constraints and one-sided interpretations tied to physical meaning (binding versus unbound). Cowan et al. explicitly treat these cases by defining modified test statistics and deriving non-standard asymptotic distributions rather than directly invoking a regular \\(\\chi^2\\) law. This highlights that “Wilks by default” is not the most defensible approach in boundary situations. The reviewed paper does not show an analogous boundary-aware derivation for its test statistics. As a consequence, the nominal sigma values and CL statements are not fully justified by standard asymptotic theory.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|10|GPT|3", "source": "prb", "split": "test", "paper_id": "prb10", "comment": "This paper’s conclusion that the observed peak is “strongly” indicative of an isoscalar \\(T_{cc}^+\\) relies on assumptions about isotriplet mass splittings and (critically) equal production of the hypothetical isotriplet components; without a dedicated quantitative limit that relaxes those assumptions, the isospin assignment is less robust than claimed.\n\n“However, an alternative interpretation could be that this state is the \\( I_3 = 0 \\) component of a \\( \\hat{T}_{cc} \\) isotriplet (\\( \\hat{T}_{cc}^0, \\hat{T}_{cc}^+, \\hat{T}_{cc}^{++} \\)) … Assuming that the observed peak corresponds to the \\( \\hat{T}_{cc}^+ \\) component and using the estimates for the \\( \\hat{T}_{cc} \\) mass splitting from Methods Eq. (M30), the masses of the \\( \\hat{T}_{cc}^0 \\) and \\( \\hat{T}_{cc}^{++} \\) states are estimated to be”\nThe paper appropriately acknowledges an isotriplet alternative, but the subsequent reasoning depends on a specific mass-splitting estimate imported from a simplified model in Methods. If that mass-splitting estimate is off by even a few MeV, the experimental signatures and widths of the partner states (especially near threshold) can change qualitatively, affecting whether they would be visible as “narrow signal-like structures.” This means the strength of the isoscalar conclusion is entangled with an auxiliary theoretical estimate rather than being derived purely from data. The manuscript does not provide a sensitivity study showing how the partner-search conclusions vary with alternative plausible mass splittings or widths. As a result, the inference that the data disfavor the isotriplet scenario is not purely experimental but conditional on modeling assumptions. That conditionality is not made explicit in the strength of the concluding language.\n“With these mass assignments, assuming equal production of all three \\( \\hat{T}_{cc} \\) components, the \\( \\hat{T}_{cc}^0 \\) state would be an extra narrow state … and increase the signal in the D^0D^0 mass spectrum by almost a factor of three.”\nThe key phrase “assuming equal production” is a strong and nontrivial assumption for hadron production in pp collisions, especially for near-threshold, possibly loosely bound states where production can be sensitive to charge states, thresholds, and phase space. The paper does not justify this assumption with data-driven arguments or simulations that demonstrate equal production within uncertainties. If the production rates are not equal, the predicted enhancement (“almost a factor of three”) can be substantially reduced, weakening the exclusion power of the D^0D^0 spectrum. Moreover, the detectability of a partner also depends on acceptance and reconstruction efficiency differences between final states, which are not quantified in the quoted reasoning. Thus, the evidentiary force of the partner non-observation is contingent on an unvalidated production hypothesis. This makes the “disfavour” claim less definitive than it appears.\n“The absence of any signals in the \\( \\mathrm{D}^+ \\mathrm{D}^+ \\) and \\( \\mathrm{D}^+ \\mathrm{D}^0 \\pi^+ \\) mass spectra is therefore a strong argument in favour of the isoscalar nature of the observed peak in the \\( \\mathrm{D}^0 \\mathrm{D}^0 \\pi^+ \\) mass spectrum.”\nThis sentence is the paper’s strongest language on isospin, but it follows from a chain of assumptions about partner masses, widths, decay modes, and production rates. Non-observation is informative, yet calling it a “strong argument” requires demonstrating that the analysis would have had adequate sensitivity under a wide range of plausible isotriplet scenarios, not only under the equal-production benchmark. The manuscript does not provide explicit upper limits (with efficiencies) on \\(\\hat{T}_{cc}^{++}\\) and \\(\\hat{T}_{cc}^{0}\\) production relative to the observed signal, which is standard practice when non-observation is used as discriminating evidence. Without those quantitative limits, it is difficult to assess how strongly the data disfavor the isotriplet interpretation versus simply being insensitive to it. Additionally, the paper itself notes that wider partner contributions would be “more difficult to disentangle from the background,” which further weakens the certainty implied by “strong argument.” Therefore, the isoscalar inference is presented with more confidence than the evidence supports.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|10|GPT|4", "source": "prb", "split": "test", "paper_id": "prb10", "comment": "This paper’s discussion of track-multiplicity dependence as an internal-structure discriminator is undermined by (i) an insufficiently justified theoretical expectation for multiplicity suppression for such states and (ii) a lack of methodological detail for the reported p-values comparing multiplicity distributions, weakening the robustness of the stated “unexpected” production behaviour.\n\n“For high-energy hadroproduction of a state with such a large size, \\( R_a \\) or \\( R_{\\Delta E} \\), one expects a strong dependency of the production rate on event multiplicity, similar to that observed for the \\( \\chi_{c1}(3872) \\) state [137].”\nThe manuscript motivates a structural interpretation by asserting a fairly specific expectation about multiplicity dependence for large-size states, but it does not derive or validate this expectation within the paper’s own framework. In hadronic collisions, multiplicity dependence can arise from multiple mechanisms (underlying event, MPI, event activity biases, selection/trigger effects), and translating a “large spatial size” into a definite suppression pattern is not straightforward without a dedicated production model. The cited analogy to \\(\\chi_{c1}(3872)\\) is suggestive, but even for X/\\(\\chi_{c1}(3872)\\) the relation between prompt production and molecular size is debated in the literature. Because the paper later observes the opposite trend (no suppression), the initial expectation becomes a linchpin for interpreting the “surprise.” Without a more explicit theoretical or simulation-backed argument, the inference risks being circular or at least weakly grounded. This limits the interpretability of the production observation.\n“A \\( p \\)-value for the consistency of the track multiplicity distributions for \\( T_{cc}^+ \\) production and low-mass \\( D^0\\overline{D}^0 \\) pairs is found to be 0.1%.”\nThe paper reports a precise p-value, but does not specify the test statistic used (e.g., \\(\\chi^2\\), KS, likelihood-ratio), whether the comparison is binned or unbinned, or how uncertainties from background subtraction and normalization are propagated into the p-value calculation. In particle-physics practice, p-values for distribution comparisons are highly sensitive to these choices, especially with weighted (sPlot-like) background subtraction and correlated uncertainties across bins. The quoted p-value is also presented alongside additional p-values in the same paragraph, raising multiple-testing considerations that can matter for interpreting “unexpected” effects. Without methodological detail, the numerical p-values cannot be independently checked and their meaning is ambiguous. This weakens the statistical support for the production-structure narrative. A clearer statistical protocol (and ideally a robustness check across tests) is needed for such a central interpretive point.\n“The similarity between \\( T_{cc}^+ \\) production, which is inherently a single parton scattering process, and the distribution for process dominated by a double parton scattering is surprising.”\nThis conclusion depends on a strong attribution of the control samples to “single parton scattering” versus “double parton scattering,” but the paper phrases the control attribution as “presumably” earlier, indicating that it is not established experimentally within the analysis. If the control sample composition is uncertain, then interpreting similarity/difference as physically “surprising” becomes less solid. Furthermore, even if the attribution is correct on average, the selection and reconstruction of multi-charm final states can introduce common multiplicity-dependent biases. The statement also implicitly assumes that multiplicity distributions map cleanly onto production mechanisms, which is not generally guaranteed in pp collisions without a dedicated MPI model and detector-level closure tests. Because the paper does not provide such closure tests in the presented text, the “surprise” may be overstated. This reduces the reliability of the production-related conclusion.\n“It seems odd that a such a loosely bound molecule could be produced promptly (i.e. not from B decay) in a high energy hadron collision environment.” ([5](#ref5))\nThis literature statement illustrates that even for the canonical near-threshold molecular candidate \\(X(3872)\\), the connection between “large size / small binding energy” and prompt hadroproduction is theoretically nontrivial and has been debated. The reviewed paper uses an expectation of multiplicity suppression as a structural diagnostic, but the broader literature indicates that production systematics for loosely bound states are complex and not universally agreed upon. Therefore, a claim of an “expected” strong multiplicity dependence should be backed by a more explicit model or by showing that alternative plausible pictures would not change the qualitative expectation. The fact that the reviewed analysis finds no suppression could reflect limitations of the heuristic expectation rather than a deep dynamical surprise. This suggests the paper’s production-based structural reasoning needs stronger theoretical anchoring. The quote supports that the field does not treat such production expectations as settled.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|10|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb10", "comment": "The paper concludes that the $T_{cc}^+$ is likely a large molecular state based on the scattering length and binding energy, but fails to reconcile this with the observed production properties which contradict this interpretation.\n\n\"The real part of the scattering length $a$ is negative indicating attraction. This can be interpreted as the characteristic size of the state [8], $R_a \\equiv -\\Re a = 7.16 \\pm 0.51 \\text{ fm} .\"\nThe analysis of the scattering length suggests that the $T_{cc}^+$ state has a very large characteristic size of approximately 7 fm, which strongly supports a loosely bound molecular interpretation.\n\"The $\\chi_{c1}(3872)$ production cross-section is suppressed with respect to the conventional charmonium state $\\psi(2S)$ at large track multiplicities [137]. It is noteworthy that the track multiplicity distribution for the $T_{cc}^+$ state differs from that of the low-mass $D^0\\overline{D}^0$ pairs, in particular no suppression at large multiplicity is observed.\"\nLarge, loosely bound molecules like the $\\chi_{c1}(3872)$ are expected to be suppressed in high-multiplicity events due to breakup interactions with comoving particles. The absence of such suppression for the $T_{cc}^+$, despite its even larger estimated size, presents a significant physical contradiction.\n\"The similarity between $T_{cc}^+$ production, which is inherently a single parton scattering process, and the distribution for process dominated by a double parton scattering is surprising.\"\nThe paper notes that the $T_{cc}^+$ production behaves similarly to Double Parton Scattering (DPS) processes (like non-resonant $D^0D^0$ production) rather than Single Parton Scattering (SPS). This behavior is unexpected for a single particle state and remains unexplained, challenging the consistency of the molecular picture which implies fragility.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|10|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb10", "comment": "The exclusion of the isotriplet hypothesis relies heavily on model-dependent theoretical mass splitting estimates rather than a robust experimental limit.\n\n\"Assuming that the observed peak corresponds to the $\\hat{T}_{cc}^+$ component and using the estimates for the $\\hat{T}_{cc}$ mass splitting from Methods Eq. (M30), the masses of the $\\hat{T}_{cc}^0$ and $\\hat{T}_{cc}^{++}$ states are estimated to be... $m_{\\hat{T}_{cc}^0} - (m_{D^0} + m_{D^{*0}}) = -2.8 \\pm 1.5\\ \\mathrm{MeV}/c^2$\"\nThe search windows and expectations for the isotriplet partners are defined based on specific theoretical estimates of the mass splittings (derived from Coulomb and quark mass differences). If the actual mass splittings deviate from these model-dependent estimates, the partners could lie outside the expected regions or have different kinematic properties.\n\"The mass spectra for $D^+D^+$ and $D^+D^0\\pi^+$ combinations are shown in Fig. 5. Neither distribution exhibits any narrow signal\"\nWhile the paper reports the absence of a signal, it does not provide a quantitative upper limit on the production cross-section of the hypothetical isotriplet partners relative to the $T_{cc}^+$ as a function of mass. A quantitative exclusion curve would be necessary to robustly rule out the isotriplet hypothesis independently of the specific mass splitting prediction.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|10|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb10", "comment": "The extraction of the pole position and scattering parameters is performed using a specific unitarised Breit-Wigner model without a comprehensive assessment of the systematic uncertainty arising from the choice of the parameterization.\n\n\"A unitarised Breit–Wigner profile $\\mathcal{F}^U$, described in Methods Eq. (M9), is used in this analysis.\"\nThe extraction of pole positions and scattering parameters near a threshold is known to be sensitive to the specific parameterization used (e.g., the choice of form factors, cutoff functions, or the order of the effective range expansion).\n\"The power-law cut-off function $f_C^P(s)$ with parameters $x_c = m_{D^0} + m_{D^+}$ and $\\sigma_c = 1$ MeV/$c^2$ is chosen.\"\nThe analysis fixes certain model ingredients, such as the cutoff function in the analytic continuation. While the paper checks consistency with a simple Breit-Wigner, it does not systematically explore alternative valid unitarisation schemes or form factors. This leaves the potential model-dependent bias in the precise values of the scattering length and effective range unquantified.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|10|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb10", "comment": "[Overall Significance] This manuscript present a detailed study for the recently observed Tcc state by the LHCb collaboration (arXiv:2109.01038). The results in my opinion, original but not significant, and they are only of interest to a special filed instead of a wider community. The most important conclusion is that the Tcc might be a hadronic molecule. However, the conclusion itself are not solid enough. The multiplicity dependent production yield of Tcc is different from molecule expectation, and the DOD*+ intermediate state need further supporting studies. The authors have credit previous work properly.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|10|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb10", "comment": "[Strength of the claims] Page 6, parametrization of background: when you use a 3-body phase space background shape, I assume your signal significance will be reduced. Please give these details here.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|10|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb10", "comment": "[Strength of the claims] Page 8, Discussion, Line 7: may you give the resolution of D*+ here, which is quite relevant to your \\delta m measurement?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|10|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb10", "comment": "[Strength of the claims] Page 8, Discussion, paragraph 2: From Extended Data Fig. 10, I think it’s difficult to make the conclusion that D0pi come from D*+. It’s quite possible there are D0D0 resonance too, as from the Dalitz plot. From the current analysis, it’s hard to judge whether the intermediate state come from D0D0 resonance or D*0 resonance.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|10|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb10", "comment": "[Strength of the claims] Page 9, paragraph 1: The discussion about D+D*0 seems lack of enough supporting, without reconstruction of pi^0 or gamma. It’s difficult to convince the audience the D+D0 peak come from D+D*0 resonance.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|10|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb10", "comment": "[Strength of the claims] Page 10, table 6: Here you observed 263 D0D0 events from the peak, while the Tcc events is only 186, which means the D0D0 peak not only come from Tcc, but also from other sources, e.g. Tcc^0 etc. As for the mass and yield prediction about the isospin partners, it suffers from theoretical uncertainties, and a ~1.5 times yield of D0D0 peak events might be a strong hint.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|10|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb10", "comment": "[Strength of the claims] Page 14, last paragraph: a) Is it possible to prove the D0D0bar mass enhancement come from chi_c1(3872)? By only looking at the D0D0bar mass distribution it’s difficult to judge where does it come from. b) Further, according to LHCb’s measurement, the intrinsic width of chi_c1(3872) is about 1 MeV, which is comparable to the resolution here, and thus will not make the D0D0bar mass distribution significantly wide. c) As for chi_c1(3872)->D0D0bar pi0/gamma decay, both Belle and BESIII have studied it, and the information is already quite abundant.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|10|Human_2|10", "source": "prb", "split": "test", "paper_id": "prb10", "comment": "[Strength of the claims] Page 18, paragraph 2: Is there any challenge to reconstruct D0->K3pi channel at the moment?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|10|Human_2|11", "source": "prb", "split": "test", "paper_id": "prb10", "comment": "[Reproducibility] The presentation of the manuscript is almost clear, after some necessary modifications (see my comments above). It’s difficult to reproduce the work. However, in order to strengthen the claims that Tcc decay are dominated by D* component and there is no isospin partner, it’s important for other experiments such as Belle/Belle II to reproduce the D+D*0 decay mode.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|10|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb10", "comment": "[Strength of the claims] Bottom page 4 through 5. The claim is made that the FWHM for the two signal models used in the analysis are consistent. I have read through these paragraphs a few times and have a feel for what is being attempted here but I still cannot figure out exactly what is being done or claimed. This section needs to be rewritten to clarify exactly how these quantities are consistent, a sketch or cartoon may be of assistance.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|10|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb10", "comment": "[Strength of the claims] Figure 3: Has a legend that shows a background contribution where the fit results in a negligible background contribution. This makes the plot confusing, at.a minimum a comment needs to be added to the legend to explain this.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|10|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb10", "comment": "[Strength of the claims] Fig 9. The top plot contains a suppressed zero which has not been commented on or signified in the axis. Either add a comment or explicitly add a signifier to show the zero is suppressed.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|Claude|1", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "The paper draws conclusions about the magnetic field structure being consistent with a \"shock-compressed magnetic field model\" despite explicitly not performing absolute EVPA calibration, which is a prerequisite for such physical interpretations in VLBI polarimetry.\n\n\"As the observing period was only 2 hours, the primary focus was on inferring the intensity and the location of the polarised emission; calibration of absolute electric vector position angle (EVPA) was not attempted since it would decrease already short total exposition on the target source.\"\nThe paper explicitly acknowledges that absolute EVPA calibration was not performed. Standard VLBI polarimetry methodology requires EVPA calibration to establish the absolute orientation of the electric field vectors, which is essential for relating the observed polarization pattern to the underlying magnetic field structure. Without this calibration, the observed EVPA values have an unknown offset that renders physical interpretation of magnetic field geometry unreliable.\n\"While specific orientation of the EVPA cannot be treated physically due to the absence of its calibration, the orderly distributed electric vectors are consistent with the shock-compressed magnetic field model.\"\nDespite the acknowledged absence of EVPA calibration, the paper still draws a physical conclusion about consistency with the shock-compressed magnetic field model. The \"orderly distribution\" of uncalibrated EVPAs cannot be reliably used to infer magnetic field topology because the relationship between EVPA and magnetic field direction depends on the absolute calibration. Without knowing the true EVPA values, one cannot determine whether the magnetic field is parallel or perpendicular to the jet axis, nor whether it is toroidal, poloidal, or randomly oriented.\n\"Absolute calibration of the electric position vector angle (EVPA) was applied using single dish observations from the Effelsberg telescope on the same day as our observations... The error in the EVPA calibration is estimated to be around 10 degrees.\" [[1]](#citation-list)\nThis quote from a recent space VLBI study of 3C 279 demonstrates the standard practice in the field: absolute EVPA calibration is performed using contemporaneous single-dish observations, and even then has uncertainties of ~10 degrees. The J0906+6930 paper lacks this calibration step entirely, making the magnetic field interpretations significantly less reliable than those achieved in similar studies.\n\nReferences:\n[1] [Fuentes et al. (2025), \"Revisiting 3C 279 jet morphology with space VLBI at 26 GHz,\" Astronomy & Astrophysics](https://www.aanda.org/articles/aa/pdf/2025/12/aa55188-25.pdf)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|Claude|2", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "The paper derives two Doppler factor estimates (δ = 6.1 ± 0.8 from brightness temperature and δ_var = 4.8 from variability) that differ by ~27%, yet uses only the higher value for deriving physical parameters (Lorentz factor, viewing angle) without adequately addressing this discrepancy or incorporating it into the uncertainty analysis.\n\n\"The T_B of the J0906+6930 core is (30.2 ± 4.0) × 10^10 K with a consequent Doppler factor δ = T_B/T_B,eq of 6.1 ± 0.8\"\nThis Doppler factor is derived by assuming the source is exactly at equipartition (T_B,eq = 5 × 10^10 K), and that any excess brightness temperature is entirely due to Doppler boosting. This assumption may not hold precisely, as intrinsic brightness temperatures can vary depending on the source conditions and magnetic field configuration.\n\"The corresponding Doppler factor is δ_var = ∛(T_B,var/T_B,eq) = 4.8\"\nThe variability-based Doppler factor of 4.8 is approximately 21% lower than the brightness temperature-based value of 6.1. This ~1.3 difference is outside the quoted error bars of ±0.8 for the first estimate, suggesting the methods may be probing different aspects of the source or that systematic uncertainties are underestimated.\n\"This value is consistent but marginally lower than that derived from the above VLBI model fitting.\"\nThe paper dismisses the 27% discrepancy as \"consistent but marginally lower\" without providing statistical justification. When two independent methods give systematically different results, this typically indicates unaccounted systematic uncertainties. The paper then proceeds to use only δ = 6.1 for calculating Γ = 3.6 and θ = 6.8°, without propagating the uncertainty from the δ_var = 4.8 value into the final parameter estimates. Using δ = 4.8 instead would yield Γ ≈ 3.3 and θ ≈ 9°, which would affect the conclusions about the jet's power and nascent nature.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|Claude|3", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "The negative proper motion of component J1 (μ = -0.006 ± 0.004 mas/yr, corresponding to -0.8 ± 0.5 c) has a statistical significance of only ~1.5σ and is consistent with zero within errors, yet is used as key evidence supporting the jet-ISM interaction and \"stationary\" jet component interpretation.\n\n\"The proper motion of J1 is −0.006 ± 0.004 mas yr^−1 (–0.8±0.5 c, Figure 3), consistent with a scenario involving jet–ISM interaction and the subsequent jet bending.\"\nThe quoted proper motion has an uncertainty of ±0.004 mas/yr, giving a signal-to-noise ratio of only 1.5 (0.006/0.004). At this significance level, the measurement is consistent with zero motion, positive motion (outward), or even the reported negative motion (inward toward core). A negative proper motion would imply the jet component is moving backward toward the core, which is physically unusual and not discussed in the paper.\n\"The position of J1 (projected distance ~5.3 pc away from the core) is nearly stationary between 2004 and 2018, consistent with a jet beam encountering dense surrounding ISM.\"\nWhile \"nearly stationary\" is a reasonable interpretation given the low significance of the measured motion, the paper uses this observation as primary evidence for jet-ISM interaction. The statistical evidence is weak: at 1.5σ, there is approximately a 13% probability that the true proper motion is positive (outward motion) rather than negative or zero. More conservative language acknowledging this substantial uncertainty would be appropriate.\n* Quote (from Supplementary Table 5): \"μ(R) = −0.006±0.004\" for J1, and \"The significance of μ(Dec, J2) is larger than 3σ\"\nThe paper appropriately notes that J2's proper motion is significant at >3σ, contrasting with J1's measurement. However, the subsequent physical interpretations rely heavily on J1's behavior despite its low statistical significance. The MOJAVE survey [[2]](#citation-list), which provides systematic proper motion measurements for a large sample of AGN jets, typically identifies reliable kinematics from measurements with higher statistical significance. Drawing firm physical conclusions from individual component motions at only 1.5σ significance should be approached with appropriate caveats.\n\nReferences:\n[2] [Lister, M. L. et al. (2019), \"MOJAVE XVII. Jet Kinematics and Parent Population Properties of Relativistically Beamed Radio-Loud Blazars,\" The Astrophysical Journal, 874, 43](https://ui.adsabs.harvard.edu/abs/2019ApJ...874...43L)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|Claude|4", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "The ISM density estimate (n_e ≥ 26.6 cm^−3) depends critically on the jet luminosity calculation, which uses empirical scaling relations with quoted uncertainties of ±2 in logarithm (a factor of 100), yet this substantial uncertainty is not adequately propagated to the derived ISM properties.\n\n\"log L_jet,rad = (12 ± 2) + (0.75 ± 0.04) log L_radio\" and \"log L_jet,kinetic = (6 ± 2) + (0.90 ± 0.04) log L_radio\"\nThe intercepts in these empirical relations have uncertainties of ±2 in log space, meaning the jet luminosity estimates from these relations have intrinsic uncertainties of a factor of ~100. This is an enormous systematic uncertainty that dominates the error budget but is not propagated through the subsequent calculations of ISM density.\n\"It must be noted that the empirical relations have a large scatter mainly due to the diversity in the sources constituting the inference, ranging from radio-loud AGN to X-ray binaries, and having to properly account for spectral state transitions, variability and systematics from comparison of data from different databases. The uncertainty on the jet power may then be underestimated.\"\nThe paper acknowledges this limitation in a single sentence but does not quantify how this affects the downstream conclusions. The ISM density calculation (n_e ≥ 26.6 cm^−3) is presented as a constraint without confidence intervals that incorporate the ±2 log uncertainty in the jet luminosity relations. Given the factor of ~100 uncertainty in jet power, the ISM density constraint could plausibly range over two orders of magnitude.\n\"ρ_ISM ≥ 2.4 × 10^−26 g cm^−3 which corresponds to a number density n_e ≥ 26.6 cm^−3\"\nThis lower limit is presented as a firm physical constraint used to support the jet-ISM interaction scenario. However, given the factor of ~100 uncertainty in the jet luminosity, and the momentum flux balance equation's dependence on L_jet, the true lower limit on n_e could be significantly different. The interpretation that \"a relatively lighter jet susceptible to interaction and bending owing to a relatively denser medium\" is weakened by these unquantified systematic uncertainties.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|GPT|1", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "This paper’s quantitative claims about the jet power relative to Eddington are internally inconsistent, weakening the validity of the central conclusion that J0906+6930 hosts a “less powerful” jet undergoing a transition in feedback mode.\n\n“The lower Lorentz factor and slower jet component are consistent with the less powerful nature of the J0906+6930 jet (jet/Eddington luminosity \\( \\sim 0.004 \\), see Methods jet and ISM properties).”\nThis sentence makes the jet/Eddington ratio a key quantitative support for the paper’s “less powerful jet” interpretation, which is then used to motivate broader physical conclusions about feedback mode transitions. Because the paper relies on this ratio for interpretation rather than treating it as a side calculation, any inconsistency in how it is computed directly affects the soundness of the conclusions. The cited value (\\(\\sim 0.004\\)) implicitly requires a consistent definition of both \\(L_{\\rm jet}\\) and \\(L_{\\rm Edd}\\), and clarity about whether beaming corrections are applied. If different sections use different definitions without reconciliation, readers cannot tell which physical regime the source is claimed to occupy. This is a major issue because jet power is central to the claimed evolutionary scenario.\n“The jet luminosity is taken as the addition of the radiative and kinetic contributions and is \\( L_{\\text{jet}} = 2.8 \\times 10^{46} \\) erg s\\(^{-1}\\), and is \\( 2.2 \\times 10^{43} \\) erg s\\(^{-1}\\) using \\( \\delta = 6.0 \\) as inferred in Appendix F. This is ~0.02 \\( L_{\\text{edd}} \\), where \\( L_{\\text{edd}} = (1.3 \\times 10^{47} \\) erg s\\(^{-1}\\))\\( m_g \\) is the Eddington luminosity and using \\( m_g = 4.4 \\times 10^{-2} \\) as inferred from Appendix H.”\nThis passage simultaneously reports two values of \\(L_{\\rm jet}\\) that differ by about three orders of magnitude, but then asserts a single ratio to \\(L_{\\rm Edd}\\) (“~0.02”) without specifying which \\(L_{\\rm jet}\\) value is used. Moreover, using the paper’s stated \\(L_{\\rm Edd}=1.3\\times 10^{47}\\,m_g\\) erg s\\(^{-1}\\) and \\(m_g=4.4\\times 10^{-2}\\) implies \\(L_{\\rm Edd}\\approx 5.7\\times 10^{45}\\) erg s\\(^{-1}\\); then \\(2.8\\times 10^{46}\\) erg s\\(^{-1}\\) corresponds to \\(\\sim 4.9\\,L_{\\rm Edd}\\), while \\(2.2\\times 10^{43}\\) erg s\\(^{-1}\\) corresponds to \\(\\sim 3.9\\times 10^{-3}\\,L_{\\rm Edd}\\). Neither matches “~0.02,” and only the smaller value is near the \\(\\sim 0.004\\) ratio claimed in the main text. Because the paper explicitly acknowledges large scatter in the empirical jet-power relations, the lack of a consistent, transparent ratio calculation makes the inferred jet weakness and feedback-transition narrative unreliable. This is not a minor numerical typo: it changes whether the jet is interpreted as sub-Eddington, near-Eddington, or super-Eddington.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|GPT|2", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "This paper’s interpretation of parsec-scale jet kinematics (including an inward/negative proper motion for J1 and derived Lorentz factor/viewing angle) is not robust because it depends on low-significance linear trends and assumes a stationary, well-defined core despite explicit evidence of core blending and structural variability.\n\n“Combining the archival and new data, the proper motion of J1 is \\( -0.006 \\pm 0.004 \\) mas yr\\(^{-1}\\) (–0.8±0.5 c, Figure 3), consistent with a scenario involving jet–ISM interaction and the subsequent jet bending.”\nThe reported J1 proper motion is only about 1.5σ from zero, so it is statistically consistent with no motion (or modest outward motion) at conventional significance thresholds. Treating such a marginal trend as “consistent with” a specific physical mechanism (jet–ISM interaction producing inward motion) overstates what the data can support, especially given sparse sampling over long time baselines. Because the claimed low bulk Lorentz factor and “less powerful jet” interpretation depend on the jet-speed estimates, the weakness of the proper-motion significance propagates into key conclusions. In VLBI kinematics studies, low-significance motions are typically reported as upper limits or treated cautiously unless supported by clear component tracking across many epochs. Here the paper’s narrative uses J1’s sign (negative) as qualitative evidence, which is not statistically justified.\n“Doppler beaming in the relativistic jet can cause the core brightness temperature (\\( T_B \\)) to exceed the theoretical limits set by equipartition between the kinetic and magnetic energy densities, assumed to be \\( T_{B,\\text{eq}} = 5 \\times 10^{10} \\) K\\(^{32}\\). The \\( T_B \\) of the J0906+6930 core is \\( (30.2 \\pm 4.0) \\times 10^{10} \\) K with a consequent Doppler factor \\( \\delta = T_B/T_{B,\\text{eq}} \\) of 6.1 ± 0.8 (see Methods Doppler boosting parameters). From the inferred apparent velocity and Doppler factor, the bulk Lorentz factor \\( \\Gamma = 3.6 \\pm 0.5 \\) and inclination angle towards the observer line of sight \\( \\theta = 6.^{\\circ}8 \\pm 2.^{\\circ}2 \\).”\nThis passage is the basis for the paper’s quantitative inference of \\(\\Gamma\\) and \\(\\theta\\), and it explicitly ties those parameters to an “inferred apparent velocity.” In the same paper, the apparent velocity is derived from sparse multi-epoch component separations that include low-significance trends (e.g., μ(J1) only ~1.5σ from zero) and noticeable short-timescale scatter (e.g., J2 between 2017 and 2018). If \\(\\beta_{\\rm app}\\) is not robust to component identification and core-centroid systematics, then the derived \\(\\Gamma\\) and \\(\\theta\\) cannot be treated as robust either, because they are computed from \\(\\delta\\) and \\(\\beta_{\\rm app}\\) via relativistic transformations. The quoted uncertainties for \\(\\Gamma\\) and \\(\\theta\\) appear to reflect propagated statistical errors, but not the dominant systematics emphasized elsewhere in the methods. This matters because the paper uses the resulting low \\(\\Gamma\\) to argue that the jet is intrinsically weak compared to typical blazars. Without demonstrating that \\(\\beta_{\\rm app}\\) is stable under alternative model fits and cross-identifications, the kinematic and physical inferences are not secure.\n“The positions of jet components are measured with respect to the core which is assumed to be stationary. The statistical error on the position is \\( \\sigma_{p,\\text{sta}} = \\frac{\\theta}{2 \\times \\text{SNR}} \\), where \\( \\theta \\) is taken as the synthesized beam size (the full width at half maximum, FWHM). As mentioned above, the core component is likely mixed with inner jet emission. In reality, the peak emission of the core can be affected by intrinsic changes of the emission structure (for example, the ejection of a new jet component or a passing shock) and the goodness of the intensity distribution being fitted with a Gaussian function. All these factors may introduce an additional uncertainty to the reference point. We have fitted the core with several different models: a single elliptical Gaussian; one circular Gaussian component (the core) plus a point source (to represent the residual emission from the unresolved inner jet); two circular Gaussian components; two point sources. The discrepancy between the fitted core positions is used as the systematic error of the reference point \\( \\sigma_{p,\\text{sys}} \\), which is added into the total error budget. The positional error of jet component can be expressed as \\( \\sigma_p = \\sqrt{\\sigma_{p,\\text{sta}}^2 + \\sigma_{p,\\text{sys}}^2} \\). We found that the positional error of the brighter component J1 is dominated by the systematic error, while the statistical error contributes a significant fraction to the positional error of J2. The positional errors of J1 and J2, as well as the derived proper motions are tabulated in Supplementary Tables 3–5.”\nThis methods description directly acknowledges that the core is not a clean, invariant reference point, because it is blended with inner jet emission and can shift with structural changes or fitting degeneracies. When the reference point itself is uncertain, small apparent inward motions of downstream components can be produced by core-centroid variability rather than true component motion. The paper attempts to handle this via model-dependent “systematic error,” but this does not guarantee that the reference point is stable across epochs separated by many years, especially when the data quality differs strongly between 2004–2005 and 2017–2018. The fact that J1’s error budget is dominated by systematic effects makes its marginal motion particularly vulnerable to these reference-point issues. As a result, interpreting the sign of J1’s motion as physical is not robust.\n```html\n  <tr>\n    <td rowspan=\"3\">2005 03 22 & 2005 05 15</td>\n    <td>C</td>\n    <td>122.7±6.4</td>\n    <td>0.209±0.001</td>\n    <td>0.067±0.002</td>\n    <td>55.3±0.1</td>\n    <td>-</td>\n    <td>-</td>\n    <td>31.0±1.8</td>\n  </tr>\n  <tr>\n    <td>J1</td>\n    <td>8.4±0.6</td>\n    <td>0.267±0.007</td>\n    <td>-</td>\n    <td>-</td>\n    <td>0.944±0.052</td>\n    <td>224.7±0.2</td>\n    <td>-</td>\n  </tr>\n  <tr>\n    <td>J2</td>\n    <td>1.9±0.3</td>\n    <td>0.321±0.053</td>\n    <td>-</td>\n    <td>-</td>\n    <td>1.290±0.061</td>\n    <td>179.8±1.3</td>\n    <td>-</td>\n  </tr>\n  <tr>\n    <td rowspan=\"3\">2017 09 11</td>\n    <td>C</td>\n    <td>43.4±2.3</td>\n    <td>0.260±0.001</td>\n    <td>0.032±0.001</td>\n    <td>49.4±0.1</td>\n    <td>-</td>\n    <td>-</td>\n    <td>18.0±1.1</td>\n  </tr>\n  <tr>\n    <td>J1</td>\n    <td>20.4±1.1</td>\n    <td>0.291±0.001</td>\n    <td>-</td>\n    <td>-</td>\n    <td>0.814±0.049</td>\n    <td>222.2±0.1</td>\n    <td>-</td>\n  </tr>\n  <tr>\n    <td>J2</td>\n    <td>1.0±0.1</td>\n    <td>0.270±0.033</td>\n    <td>-</td>\n    <td>-</td>\n    <td>1.568±0.053</td>\n    <td>184.6±0.1</td>\n    <td>-</td>\n  </tr>\n  <tr>\n    <td rowspan=\"3\">2018 01 31</td>\n    <td>C</td>\n    <td>41.8±2.2</td>\n    <td>0.249±0.004</td>\n    <td>>0.034</td>\n    <td>52.2±1.3</td>\n    <td>-</td>\n    <td>-</td>\n    <td>>17.1</td>\n  </tr>\n  <tr>\n    <td>J1</td>\n    <td>18.0±1.0</td>\n    <td>0.170±0.001</td>\n    <td>-</td>\n    <td>-</td>\n    <td>0.801±0.071</td>\n    <td>222.8±0.1</td>\n    <td>-</td>\n  </tr>\n  <tr>\n    <td>J2</td>\n    <td>1.4±0.2</td>\n    <td>0.444±0.079</td>\n    <td>-</td>\n    <td>-</td>\n    <td>1.435±0.076</td>\n    <td>184.8±0.9</td>\n    <td>-</td>\n  </tr>\n```\nThese Table 1 rows show that the fitted core–J1 separation decreases from 0.944±0.052 mas in 2005 to 0.814±0.049 mas in 2017 and 0.801±0.071 mas in 2018, which is the sole basis for the reported negative μ(J1). The absolute change (~0.14 mas over >12 yr) is small compared with typical 15 GHz VLBA beam sizes and with the core-centroid systematics the paper itself emphasizes, so the sign of the slope is sensitive to modeling choices. The same table shows that J2’s separation changes from 1.568±0.053 mas (2017) to 1.435±0.076 mas (2018) over only a few months, highlighting that component centroids can shift appreciably even within the ‘new’ epoch pair. Such short-timescale scatter suggests that a simple linear regression across sparse epochs may not capture true ballistic motion and may instead absorb structural variability or mis-identification. Given that the paper uses these separations to claim both inward motion (J1) and a representative apparent speed (J2), the kinematic interpretation is not robust without stronger cross-identification tests. At minimum, the evidence supports only weak constraints (or upper limits) on proper motions rather than the mechanistic conclusions drawn.\n“In all cases, we assume the bright core feature (id = 0 in Table 3) to be stationary, and measure the positions of jet features at all epochs with respect to it.” ([\\[4\\]](#ref4))\nThis standard practice in large VLBI kinematics surveys is explicitly an assumption, not a guarantee, and its validity depends on the core being a stable feature and on careful cross-identification of components. The reviewed paper’s own methods section notes that the core can be blended and variable, which is exactly the situation where this assumption becomes problematic. In the MOJAVE analysis, inward motions are treated as rare and can be attributed to centroid shifts or core mis-identification, underscoring that apparent inward motion requires careful scrutiny rather than immediate physical interpretation. By contrast, the reviewed paper uses a marginally significant inward μ(J1) as supportive evidence for jet–ISM interaction without an equally strong validation of component identity and core stability. This discrepancy indicates the kinematic inferences are not as robust as common practice would require.\n“Accurate measurement of the frequency-dependent shift of the self-absorbed radio core is required for multi-frequency analysis of VLBI data since absolute positional information is lost as a result of phase self-calibration.” ([\\[3\\]](#ref3))\nWhile the reviewed paper measures relative separations rather than absolute astrometry, this quote highlights a closely related methodological limitation: self-calibration removes external positional constraints, so the inferred core position becomes model-dependent and can shift with opacity or structural changes. In a study where proper motions are at the few microarcseconds per year level, any small systematic drift in the fitted core centroid can dominate the inferred component motion, especially over long baselines. The reviewed paper acknowledges structural blending in the core, which makes core-centroid shifts plausible even at a single frequency. Without phase-referenced astrometry or an explicit image-registration/core-stability analysis, the paper cannot confidently attribute small inward trends to physical jet dynamics. This undermines the reliability of the reported low proper motion and derived jet parameters.\n“If the VLBA target source is not sufficiently strong for self-calibration or if absolute positional information is needed but geodetic techniques are not used, then VLBA phase referenced observations must be employed (Beasley & Conway 1995).” ([\\[2\\]](#ref2))\nThis guidance makes explicit that self-calibrated VLBA imaging does not preserve external positional information, and that phase referencing is the standard method when astrometric stability is required. In the reviewed paper, the component positions are referenced to a fitted core that is acknowledged to be blended and variable, so an independent astrometric anchor would be valuable for validating small apparent motions. The measured proper motions are at the few thousandths of a mas per year level, meaning that even sub-mas reference-point drifts can materially change the inferred slopes across a decade. Without phase-referenced observations (or an alternative registration analysis), the study cannot rule out that the apparent inward motion reflects changes in the reference core centroid rather than real component motion. This does not invalidate imaging or morphology results, but it weakens kinematic claims that hinge on the sign and magnitude of μ at the ~1–2σ level. Therefore, the lack of an astrometric constraint limits the validity of the kinematic interpretation.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|GPT|3", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "This paper’s inference of a dense ambient medium (e.g., \\(n_e \\ge 26.6\\,\\mathrm{cm}^{-3}\\) and density contrast >9) is not robust because it is derived from a highly simplified momentum-balance model fed by uncertain and internally inconsistent jet-power and kinematic inputs, without propagating uncertainties or exploring sensitivity.\n\n“The density contrast between the material in the jet and that external to it is > 9 (see Methods jet and ISM properties), thus suggesting a relatively lighter jet susceptible to interaction and bending owing to a relatively denser medium. Assuming a momentum balance across the jet–ISM interaction interface, the ISM number density is estimated to be \\( n_e \\geq 26.6 \\) cm\\(^{-3}\\).”\nThis statement elevates the density contrast and ISM density estimate to key evidence for the paper’s preferred jet–ISM interaction scenario, which also underpins the “nascent jet embedded in a dense medium” conclusion. However, the quoted values are presented as hard lower limits without showing how they change under plausible variations of jet power, jet opening angle, or jet-head speed. In VLBI-based physical inference, such environmental densities are typically highly model-dependent and require careful uncertainty propagation because multiple poorly constrained quantities enter multiplicatively. Presenting a single-point estimate as a firm lower bound risks overstating the evidence for a dense medium. This is significant because the dense-medium claim is one of the main differentiators from alternative explanations (e.g., projection/helical geometry).\n```text\nUnder conditions of an ambient ISM (non-relativistic), the momentum flux balance between the jet and the ISM \\( ^{60} \\)\n\n\\[\n\\frac{L_{\\text{jet}}}{(\\beta_{\\text{jet}} - \\beta_h)c} = \\rho_{\\text{ISM}} \\beta_h^2 c^2 A_h\n\\]\n\n(12)\n\nwhere \\( L_{\\text{jet}} \\) is the jet luminosity, \\( \\beta_{\\text{jet}} \\) is the jet speed (in units of \\( c \\)), \\( \\rho_{\\text{ISM}} \\) is the ISM density, \\( \\beta_h \\) is the speed of the advancing jet head (in units of \\( c \\)) and \\( A_h \\) is the surface area of the jet head interacting with the ISM.\n\nThe average core separation from J1, \\( r_{1}/\\sin \\theta = 43.2 \\) pc from which, the circumferential radius in contact with the ISM \\( r_h = r_{1}/2 = 21.6 \\) pc and \\( A_h \\approx r_h^2 \\sin \\theta_0 = 82.9 \\) pc\\(^2\\) assuming an intrinsic jet half-opening angle \\( \\theta_0 = 10^\\circ \\)\\(^{61}\\). The relativistic transformation,\n\n\\[\n\\beta = \\frac{\\beta_{\\perp}}{\\sin \\theta + \\beta_{\\perp} \\cos \\theta}\n\\]\n\n(13)\n\nrelates the projected transverse speed (proper motion) \\( \\beta_{\\perp} \\) with the true speed \\( \\beta \\) through the inclination angle \\( \\theta \\). The jet speed \\( \\beta_{\\text{jet}} \\sim \\beta_{12} = 0.96 \\) \\( c \\) based on a \\( \\beta_{\\perp,2} = 2.5 \\) \\( c \\) and using the above relativistic transformation. The speed of the jet head \\( \\beta_h < \\beta_{12}/4 = 0.24 \\) \\( c \\) (upper limit on the speed of the shocked expanding gas at the jet head post interaction with the ISM), assuming a strong shock interaction which entails a post shock plasma with the above maximal speed. The density contrast between the ISM and jet\\(^{60} \\) is\n\n\\[\n\\frac{\\rho_{\\text{ISM}}}{\\rho_{\\text{jet}}} = \\left( \\frac{\\beta_{\\text{jet}}}{\\beta_h} - 1 \\right)^2\n\\]\n\n(14)\nusing which \\( \\rho_{ISM}/\\rho_{jet} > 9 \\), likely resulting in the lower density jet being susceptible to a deflection or bending upon interaction with the ISM, while being able to cause a compression of the material near the jet head. Employing the above calculated quantities and the simplifying assumptions in equation (12), \\( \\rho_{ISM} \\geq 2.4 \\times 10^{-26} \\) g cm\\(^{-3}\\) which corresponds to a number density \\( n_e \\geq 26.6 \\) cm\\(^{-3}\\).\n```\nThese method statements show that the ISM density lower limit is not a direct observable but comes from a chain of assumptions: a non-relativistic ambient medium, an assumed jet-head speed bound, a chosen interaction area derived from an assumed opening angle, and a jet speed inferred from β⊥ and θ. Because each of these quantities carries substantial uncertainty (proper motions, viewing angle, opening angle, and jet-head dynamics), the derived \\(n_e\\) is highly sensitive to unreported systematics. The paper does not propagate uncertainties from β⊥, θ, or from the jet-power estimate into \\( \\rho_{\\rm ISM} \\) and \\(n_e\\), so the stated “≥” bound cannot be interpreted quantitatively. In particular, taking \\( \\beta_h < \\beta_{12}/4 \\) as an “upper limit” under a strong-shock assumption effectively fixes the density contrast to be >9, but the shock strength and jet-head physics are not constrained by the presented data. As a result, the calculation cannot discriminate between a genuinely dense medium and a modest-density medium combined with different jet parameters. Without sensitivity analysis, the dense-medium conclusion is not robustly supported.\n“The jet luminosity is taken as the addition of the radiative and kinetic contributions and is \\( L_{\\text{jet}} = 2.8 \\times 10^{46} \\) erg s\\(^{-1}\\), and is \\( 2.2 \\times 10^{43} \\) erg s\\(^{-1}\\) using \\( \\delta = 6.0 \\) as inferred in Appendix F. This is ~0.02 \\( L_{\\text{edd}} \\), where \\( L_{\\text{edd}} = (1.3 \\times 10^{47} \\) erg s\\(^{-1}\\))\\( m_g \\) is the Eddington luminosity and using \\( m_g = 4.4 \\times 10^{-2} \\) as inferred from Appendix H. It must be noted that the empirical relations have a large scatter mainly due to the diversity in the sources constituting the inference, ranging from radio-loud AGN to X-ray binaries, and having to properly account for spectral state transitions, variability and systematics from comparison of data from different databases\\(^{59}\\). The uncertainty on the jet power may then be underestimated.”\nThis methods passage shows that the jet power used as input to the ISM-density calculation is not well constrained, since the paper reports both \\(L_{\\rm jet}=2.8\\times 10^{46}\\) erg s\\(^{-1}\\) and a Doppler-corrected value of \\(2.2\\times 10^{43}\\) erg s\\(^{-1}\\). Because the momentum-balance equation scales linearly with \\(L_{\\rm jet}\\), the inferred \\(\\rho_{\\rm ISM}\\) and \\(n_e\\) would change by similar orders of magnitude depending on which value is used. The text further acknowledges that the empirical radio-to-jet-power relations have “a large scatter” and that the jet-power uncertainty may be underestimated, but this uncertainty is not carried through to the quoted density lower limit. As a result, presenting \\(n_e \\ge 26.6\\,\\mathrm{cm}^{-3}\\) as strong evidence for a dense environment is not justified by the paper’s own uncertainty statements. A defensible treatment would show the range of \\(n_e\\) implied by plausible \\(L_{\\rm jet}\\) and kinematic parameter intervals. Without that, the dense-medium conclusion is not robust.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|GPT|4", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "This paper draws a magnetic-field/shock interpretation from an EVPA pattern even though it explicitly states that absolute EVPA calibration was not performed, making the EVPA-based physical interpretation unsupported.\n\n“The VLBA observing project BZ071 presented in this paper was designed primarily as the preliminary exploratory attempt to detect a pc-scale polarised emission from the source. As the observing period was only 2 hours, the primary focus was on inferring the intensity and the location of the polarised emission; calibration of absolute electric vector position angle (EVPA) was not attempted since it would decrease already short total exposition on the target source.”\nThis sentence establishes that the observation and calibration strategy intentionally omitted the step needed to place EVPAs onto an absolute on-sky reference frame. That omission is reasonable for a short exploratory polarization detection experiment, but it limits what physical statements can be supported about magnetic-field orientation. Any downstream interpretation that depends on EVPA directions relative to the jet axis or sky coordinates therefore requires additional calibration that the paper did not do. In polarimetric VLBI, detecting polarized intensity alone is often feasible without absolute EVPA calibration, but interpreting field geometry usually is not. This sets up a clear methodological boundary that the paper should not cross. The subsequent text does cross it.\n“While specific orientation of the EVPA cannot be treated physically due to the absence of its calibration, the orderly distributed electric vectors are consistent with the shock-compressed magnetic field model.”\nThis sentence contains a contradiction: it correctly notes that the EVPA orientation “cannot be treated physically,” but then immediately treats the EVPA pattern as supporting a specific physical model. Shock-compressed magnetic-field interpretations generally depend on comparing EVPA orientation to the jet direction (e.g., perpendicular/parallel trends), which cannot be done if EVPA has an unknown global rotation. Even if the vectors appear “orderly,” an arbitrary constant rotation can turn an apparently jet-parallel pattern into a jet-perpendicular one, changing the physical interpretation. The paper does not demonstrate that its “orderly” pattern is invariant under the unknown EVPA offset in a way that still supports the claimed model. Therefore, the evidence is insufficient to support the shock-compression claim.\n“Furthermore, without calibration of the RCP-LCP phase difference, the polarization angle is undetermined.” ([\\[1\\]](#ref1))\nThis standard VLBA polarimetry guidance states explicitly that uncalibrated RCP–LCP phase leaves the polarization angle undefined, which is exactly the situation the reviewed paper describes for its dataset. If the EVPA is “undetermined,” then any physical interpretation that relies on its absolute direction is not warranted. The reviewed paper’s later assertion that the EVPA pattern is consistent with a shock model therefore lacks the necessary calibration support. Importantly, this is not a cosmetic calibration detail: it changes whether EVPA vectors can be compared to the jet morphology at all. The paper can still claim a detection of polarized intensity and perhaps discuss fractional polarization levels, but not EVPA-based field geometry. This evidence directly supports the methodological criticism.\n“The usual phase calibration schemes adjust the systems of parallel hand feeds to internally consistent values but allow an arbitrary phase difference between the two parallel hand systems. This converts directly into an arbitrary, but constant, rotation of the apparent orientation of the E-vectors on the sky.” ([\\[5\\]](#ref5))\nThis AIPS polarimetry memo explains the mechanism by which missing EVPA calibration leads to an arbitrary rotation of observed EVPAs, clarifying why “orderly vectors” are not, by themselves, diagnostic of a physical magnetic-field configuration. The reviewed paper’s uncalibrated EVPA map could be globally rotated by an unknown angle, meaning that the absolute relationship between EVPA and jet direction is fundamentally ambiguous. Because shock-compressed field claims typically require that relationship (e.g., EVPA aligned with/orthogonal to the jet), the paper cannot logically use the EVPA map to support that model. The memo also notes other sources of EVPA rotation such as ionospheric Faraday effects, underscoring that even with a constant offset, uncorrected propagation effects can further complicate interpretation. The reviewed paper does not provide calibrator-based anchoring or external cross-checks, so the EVPA-based conclusion is not supported. This is a significant limitation because the EVPA discussion is used as “evidence” for the jet–ISM interaction interpretation.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "The authors interpret the uncalibrated EVPA distribution as consistent with a shock-compressed magnetic field model. Since the absolute EVPA calibration is missing, the orientation of the magnetic field relative to the jet axis is unknown, making this conclusion baseless.\n\n\"While specific orientation of the EVPA cannot be treated physically due to the absence of its calibration, the orderly distributed electric vectors are consistent with the shock-compressed magnetic field model.\"\nThis statement from the Supplementary Note admits that the Electric Vector Position Angle (EVPA) is uncalibrated. A \"shock-compressed magnetic field model\" implies a specific geometric relationship between the magnetic field (and thus EVPA) and the shock front (usually perpendicular to the jet axis). Without absolute calibration, the observed EVPA could be at any angle relative to the jet, rendering the claim of consistency with any specific geometric model invalid.\n\"Polarization position angle calibration is essential for determining the intrinsic magnetic field orientation...\" [1]\nStandard VLBI practice requires calibration using a known source (like 3C 286) to determine the absolute EVPA. Without this, one cannot distinguish between a parallel, perpendicular, or oblique magnetic field, which is the key discriminator for shock models.\n\nReferences:\n[1] Homan, D. C., & Wardle, J. F. C. (2004). MOJAVE: Monitoring of Jets in Active Galactic Nuclei with VLBA Experiments. I. The First Epoch. The Astrophysical Journal Supplement Series, 154(1), 152. https://iopscience.iop.org/article/10.1086/422028", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "The proper motion of component J1 is consistent with zero ($1.5\\sigma$). The authors use this non-detection to claim a \"measurement\" of low proper motion and derive physical parameters (Lorentz factor). While an upper limit is valid, treating it as a measurement to infer specific jet properties is an overinterpretation.\n\n\"J1 ... -0.006±0.004\"\nThe error bar ($\\pm 0.004$) is comparable to the value itself ($-0.006$), resulting in a significance of only $1.5\\sigma$. In VLBI surveys like MOJAVE, a significance of $>3\\sigma$ is typically required to claim a robust proper motion measurement [2].\n\"The jet parameters (lower proper motion and bulk Lorentz factor) are inclined to support a less powerful jet\"\nThe authors derive physical conclusions (low Lorentz factor, less powerful jet) based on this marginal detection. A non-detection of motion implies an upper limit on $\\beta_{app}$, but it does not constrain the Lorentz factor tightly without assumptions about the viewing angle, and treating it as a definitive \"low proper motion\" characteristic is statistically weak.\n\nReferences:\n[2] Lister, M. L., et al. (2019). MOJAVE. XVII. Jet Kinematics and Parent Population Properties of Relativistically Beamed Radio-Loud Blazars. The Astrophysical Journal, 874(1), 43. https://iopscience.iop.org/article/10.3847/1538-4357/ab08e7", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "The conclusion that the source indicates a \"transition from an accretion radiative power to a jet mechanical power\" is speculative and based on limited evidence (a single object with a weak jet). Alternative explanations are not sufficiently ruled out.\n\n\"indicate a transition from an accretion radiative power to a jet mechanical power based transfer of energy and momentum to the surrounding gas.\"\nThis major conclusion in the Abstract is based on the observation of a weak jet in a high-accretion object. However, this could simply represent a \"radio-quiet\" or \"radio-intermediate\" state, or a misaligned jet (despite the blazar classification), rather than an evolutionary \"transition\" phase. Generalizing the state of a single object to a cosmic evolutionary phase requires a larger sample and more robust evidence of evolution.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "It is rather disturbing to see in Figure 2 the relatively strong linear polarization flux with no indication of EVPA. I see that in Appendix D the authors note that they did not attempt to get the EVPA; why not?? You made the Q and U maps; if you trust these we should have a EVPA value, if not, why do you trust your Pi? The leakage terms should be known, albeit perhaps imperfectly. The EVPA is the most important datum for physical interpretation; this is the aspect that is likely to influence scientists in this field. Thus, I believe that you should plot an EVPA estimate on Figure 2 (with all appropriate caveats), and discuss at least briefly. If the data do not allow any useful estimate, please state clearly why and why the Pi measurement is then still robust.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "The interpretation focuses on the idea that J1 is a termination shock with the deflected jet represented by J2, motivated by the apparent stable core-J1 distance. I think this is plausible, but surely there are other interpretations -- perhaps J1 and the core are two standing shocks in the outflow. So while the idea that this is a nascent jet tunneling through the host ISM is interesting, some alternatives should be mentioned. One motivation for doing this is that the present apparently substantially sub-Eddington jet luminosity may not be a characteristic state for such a large BH mass at high z. One might expect an earlier, more typical, high luminosity phase to have cleared the local ISM. Perhaps the BH has recently entered the present dense, uncleared ISM, but this seems odd.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "Related to 2): looking through the appendices it appears that the authors have been somewhat cavalier in their model estimates. Given that these are intrinsically imprecise the general conclusions may be OK, but the logic seems a bit forced. For example, they use the beta_perp~2.2 of J2 in a number of equations when evaluating the properties of the shock at J1. For example the theta ~7 deg is applied to J1 to get a true core separation. These numbers are also used in the penultimate paragraph of the main article, which further obscures that this beta_perp is being applied to the pre-J1 flow. (Also the argument around Eq 13 is circular -- beta_h was just inferred for a strong shock, which assumes the high density contrast.) These examples suggest that, at a minimum the authors need to be clearer about what they have assumed in making their estimates (e.g. small J1/J2 angle deflection, no deceleration). The authors did argue that the 2017 J1 flux was responding to the 2011 core flare. That could give an effective beta_perp estimate for pre-J1 flow of 17.3lt-y/<6y >2.9. That is crude but it does apply to J1.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "Still in Appendix H, I was somewhat puzzled why the authors used the monochromatic expression from Birzan et al. (Eq 16) in Eq 10. Since one sees an SED peak in the radio we have a ~bolometric luminosity so the bolometric expression from Birzan (Eq 13) would seem more appropriate; that gives L_j~3.4e45 erg/s and M_edd~0.03 for 10^9Msun, with the numbers quoted. A more careful integration of the rest frame radio luminosity should be used, though. On the other hand An et al (ref 25) give M as 4x10^9 Msun, which re-lowers the efficiency -- you might wish to use that mass in your estimates or at least mention it and give the scaling.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "On the subject of the radio SED peak -- this was published in Romani 2006 AJ 132, 1959. the reference used (14 = Zhang et al 2017) largely drew the data from that paper and I don't think it materially improved the spectrum measurement on that earlier result.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "The Coppejans reference in App. H should be 2016, not 2017.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|Human_1|9", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "Overall I think that this is a good paper, but it could be better. If, as the authors repeatedly note, measuring the polarization is a big deal, they should give an EVPA estimate. If the nascent jet/ISM shock argument is the most important result, the arguments about its energetics should clearer. Perhaps with a bit of attention to the points above these aspects could be improved. Publication would then be appropriate.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "Confidence intervals for the errors need to be given: 68% or 90% or (something else? If 68%, the proper motion measurement may not be significant (enough; they are only at the ~2-sigma level (95%). In this case, reporting (upper limits may be more appropriate. 2) In Appendix C, it is said that the (positional errors are 10% and 5% of FWHM of the restoring beam for J1 and J2, (respectively. As the errors may have significant impacts on the (proper motion (and other) results, these numbers need further justifications.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "The authors do not propagate measurement errors adequately when reporting other derived quantities. Some of their measurements have relatively large uncertainties (e.g., proper motion), and so their conclusions may change if considering the errors. It may be very difficult to quantify all the errors, but they need to be considered seriously when drawing conclusions.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "The bulk Lorentz factor is reported to be >3.3, only an upper limit. While this is consistent with previous estimations (e.g., Zhang et al. 2017, An & Romani 2018), it alone does not rule out a possibility of a powerful jet (as opposed to the claimed ‘less powerful jet’).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "For inferring the jet power and ISM density (Appendix H), the authors assume that the spectral index is 0 between 1.4 GHz and 15 GHz for J1 and/or J2. Although previous measurements of the radio spectrum seem to support this albeit a spectral break at ~10 GHz, the measurements are for C+J1+J2 (or C as it dominates) as compared to J1+J2. Is it reasonable to assume the same spectrum for J1+J2 when the variability of C+J1+J2 is different from that of J1 (and/or J2) in Table 3 and Figure A1? This may be a concern when extrapolating the 15-GHz flux density to 1.4-GHz. In particular, the authors mention a propagating shock. The propagating shock may change the radio spectral shape in time (e.g., Valtaoja et al. 1992), hence assuming a radio spectral index of 0 in 2017-2018 based on earlier data needs a justification. In this regard, (near) contemporaneous multi-frequency observations may be helpful.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "The empirical relation (between L_jet and P_1.4GHz) they used in Appendix H may have a relatively large uncertainty (a few orders of magnitude scatter in the data used for deriving the relation; Birzan et al. 2008); this (and other) uncertainty needs to be considered when deriving the jet power and claiming that it is low.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "The reported number n~65 cm^-3 (in the text and Appendix H) for the ISM density is too precise compared to the arguments given in Appendix H (see also comments 3-5). Shouldn’t it be a limit as is for the density contrast rho_ISM/rho_jet>11 because beta_h is only a limit?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "It is said “In the highest-resolution images, a sharp (>90 degree) jet bending is seen...” in the text. As the jet bending is seen in a previous study of the same source (e.g., Zhang et al. 2017), the previous work needs to be recognized.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "It is said “a prominent X-ray emission (with a strong contribution from the disk)..” in the text. It is believed that X-rays in these high-z blazars are produced mainly by the synchrotron-self-Compton process and that disks of supermassive blackholes mostly radiate in the optical band. Hence, the statement needs to be clarified.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|Human_2|11", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "In Appendix H, it appears that the authors consider J1+J2. This should be mentioned explicitly. Assuming J1+J2, I do not reproduce S_15GHz=21 mJy from the table. In 2017-2018, the average flux of J1 and J2 is ~20.4 mJy. The difference is only tiny, but I wonder if there is something else I am missing here.", "reviewer_type": "human", "label": "error", "error_type": "Unstated statement", "label_origin": "expert+llm-filter"}
{"id": "prb|12|Human_2|12", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "In Appendix G above equation (8) it is said “Employing equation (7) which reduces to...”. Equation (7) does not seem to reduce to (8), so this may be a mistake.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "Authors indicated J0906+6930 as the most distant known blazar, having z=5.47. However, there is a recent detection by Saxena et al. (2018, MNRAS, 480, 2733) of a jetted AGN at z=5.72. The radio spectral index suggests it could be a radio galaxy, thus with the jet viewing angle greater than ≈10°. Therefore, the authors statements are formally correct. However, I would say a few words about this other jetted AGN.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "[page 1, row 19] Authors wrote: \\\"As jetted quasars seem to harbour heavier black holes than non jetted ones, high-redshift blazars are probes...\\\". The line of reasoning is inverted. High-z quasars are useful probes for the early universe because they are the brightest sources, and, therefore, it is easier to find them. But, the extreme brightness is due to: (1) the presence of a relativistic jet viewed by a small angle, which means that the electromagnetic emission is Doppler boosted (with a typical Doppler factor of 10, the luminosity of the jet is boosted to 10000 times its isotropic value); (2) as the jet power scales with the mass of the central black hole (P proportional to M^1.4, cf Heinz & Sunyaev 2003), a larger mass implies a larger observed jet power.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "[page 1, row 28-29] the radio loudness is a meaningless parameter. No need to cite it.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "[Section F] Doppler boosting parameter of the jet. Authors estimated the Doppler factor δ by using the brightness temperature as measured from the VLBI core size. The apparent jet speed β<sub>app</sub> is measured from VLBI observations. From δ and β<sub>app</sub>, it is then possible to calculate the bulk Lorentz factor Γ and the viewing angle θ. As the authors reported also the OVRO 15 GHz radio light curve, I suggest to calculate δ also from radio variability. An easier way is to refer to Liodakis et al. (2018, ApJ, 866, 137), who already did it and reported δ=8.91. Together with β<sub>app</sub>=2.2c measured by the authors, it results Γ=4.8 and θ=3°. Please note that Liodakis calculated the equipartition brightness temperature is a way different from usual. So, when comparing your results with him, please take into account this difference. Please note that also the main text -- not only Section F -- must be changed accordingly.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "[Section H] authors calculated the jet power by using a relationship by Birzan et al. (2008). These relationships links the extended radio emission measured in the MHz frequency range with the jet kinetic power. Therefore, the application to one component detected at 15 GHz is rather risky, as it is known that extrapolating from high to low frequency could give serious errors in the estimation of the extended emission. In addition, the jet power by Birzan refers only to the kinetic component, and does not include the radiative part. The kinetic part calculated in this way is based on the cavities excavated by the jet activity during million of years and are not comparable with a year time scale as from the authors of the present essay. I suggest to adopt the relationships by Foschini (2014, Int. J. Mod. Phys. Conf. Series, 28, 1460188), which links the radiative and kinetic power to the 15 GHz core luminosity. You should apply them to the core flux, but you can also try to apply them to the component J1. Obviously, you have to address the proper caveats. A quick calculation by using the core emission, resulted in a log P<sub>rad</sub>=45.4 [erg/s] and log P<sub>kin</sub>=46.1 [erg/s], greater than the estimates from the Birzan relationship, as expected.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|12|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb12", "comment": "the last (but not least) point refers to the estimation of the mass of the central black hole and the accretion rate. Authors refer to previous works, which gave a mass of the order of 10<sup>9</sup>M<sub>Sun</sub> and accretion luminosity 0.4 times the Eddington limit. However, all the previous estimates adopted relationships made for non-jetted AGN. The presence of the Doppler boosting alters significantly the continuum emission, which implies an overestimation of the mass. Also the fit of the accretion disk suffers the same problem. As the optical spectra all show a strong Lyα emission line, I suggest to use it together the relationships by Pian et al. (2005, MNRAS, 361, 919), which take into account the Doppler boosting. Indeed, a quick calculation of the λL(1350A) by using the Pian's relationships results in a value of ≈7.4×10<sup>43</sup> erg/s to be compared with the value of 5×10<sup>47</sup> erg/s given by Romani (2004). The radius of the broad-line region (BLR) from Bentz et al. (2013), results to be 18.6 light days, which implies a luminosity of the disk of ≈3×10<sup>43</sup> erg/s. I've not found a measurement of the FWHM of Lyα, but if we assume the value of 5000 km/s from other lines, the mass of the central black hole results to be ≈ 7×10<sup>7</sup>M<sub>Sun</sub>. Therefore, I suggest to recalculate the mass and accretion rate of the central black hole by using the Lyα line parameters and Pian's relationships. Then, revise the discussion in the text according to the new values. A smaller mass of the central black hole would be more suitable for a young AGN, and also more consistent with a high-frequency peaker (HFP). Compare also with Berton et al. (2016, A&A, 591, A98).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|13|Claude|2", "source": "prb", "split": "test", "paper_id": "prb13", "comment": "The external prediction validation on the HCP dataset yields a correlation of r=0.18 between predicted and actual PSQI scores, which explains only ~3% of variance and represents a weak effect size that challenges the paper's claims of establishing a clinically useful brain connectome biomarker.\n\n\"It turned out the significant edges of the sleep-health related connectome found in the discovery sample can predict the total score of PSQI in the HCP dataset as evidenced by a significant Pearson correlation between the predicted and original PSQI (r average=0.18, r range = 0.12-0.24 permuted p<0.001)\"\nWhile statistically significant (due to the large sample size of n=435), this effect size (r=0.18) means the model explains approximately 3.24% of variance (r²=0.0324) in sleep quality. In the context of neuroimaging-based prediction, such modest effects are common but raise questions about clinical translation. Best practices for prediction in neuroimaging emphasize that statistical significance should not be conflated with practical predictive utility, and multiple measures of prediction accuracy should be reported [[2]](#citation-2).\n\"These results hence delineated a sleep health dimension whose associated functional connectome could serve as an objective neuroimaging biomarker in clinical translations\"\nThe claim that this connectome pattern can serve as an \"objective neuroimaging biomarker in clinical translations\" appears overstated given the modest prediction effect size. An r=0.18 correlation in out-of-sample prediction suggests limited practical utility for individual-level clinical decision-making, as nearly 97% of variance in sleep quality remains unexplained by the model.\n\"Importantly, we also examined the prediction performance of models using the whole brain connectome. Our results here showed that models using the specific sleep-health related connectome yield slightly higher prediction performance than whole-brain connectome models (after a 100 repeated 10-fold cross validation, r average=0.16, r range = 0.10-0.22)\"\nThe improvement from whole-brain connectome (r=0.16) to sleep-health-related connectome (r=0.18) is marginal (Δr=0.02), suggesting that the identified sleep-health-related features provide only minimal incremental predictive value beyond general brain connectivity patterns. This modest improvement further questions the specificity and utility of the proposed biomarker.\n\nReferences:\n[2] Poldrack RA, Huckins G, Varoquaux G. [Establishment of Best Practices for Evidence for Prediction: A Review](https://pubmed.ncbi.nlm.nih.gov/31774490/). JAMA Psychiatry. 2020;77(5):534-540.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|13|Claude|3", "source": "prb", "split": "test", "paper_id": "prb13", "comment": "The insomnia disorder classification achieving 79.12% accuracy relies on 10-fold cross-validation within a single dataset rather than validation on a truly independent external test set, which is inconsistent with best practices for establishing clinical diagnostic utility of neuroimaging-based AI models.\n\n\"The classifier performance was validated using a 100 repeated 10-fold cross-validation strategy... It turned out that the sleep-health related connectome also has diagnostic potential to distinguish insomnia patients from sleep healthy subjects with an average accuracy across 100 CV of 79.12% (permuted p < 0.0001)\"\nWhile 10-fold cross-validation with 100 repetitions provides some validation, all data from the classification dataset (n=101) is used in both training and testing phases across the folds. This approach does not constitute a true independent external validation, as the same distribution of samples is repeatedly used. A systematic review found that neuroimaging-based AI models for psychiatric diagnosis overwhelmingly lack proper external validation, with only 86 of 555 models (15.5%) tested on independent external samples [[1]](#citation-1).\n\"We further evaluated the possibility of distinguishing the insomnia patients (n=52) from sleep healthy controls (n=49) based on the RSFC spatial pattern of the found LV/dimension\"\nThe small classification sample size (n=101 total) is problematic for establishing reliable clinical performance estimates. With such limited data, cross-validation results can exhibit high variance. Best practices in neuroimaging prediction recommend samples of several hundred observations for reliable performance estimates, noting that \"cross-validation failure: small sample sizes lead to large error bars\" [[3]](#citation-3).\n\"Classification performance that had an accuracy of higher than 70% were considered to be meaningful.\"\nThe 70% threshold for \"meaningful\" classification is arbitrary and not justified based on clinical needs or field standards. For a diagnostic biomarker to have clinical utility, performance characteristics including sensitivity, specificity, and predictive values should be evaluated in the context of clinical decision-making requirements, not simply compared against arbitrary cutoffs.\n\nReferences:\n[1] Chen Z, Liu X, Yang Q, et al. [Evaluation of Risk of Bias in Neuroimaging-Based Artificial Intelligence Models for Psychiatric Diagnosis: A Systematic Review](https://jamanetwork.com/journals/jamanetworkopen/fullarticle/2801999). JAMA Netw Open. 2023;6(3):e231671.\n[3] Varoquaux G. [Cross-validation failure: Small sample sizes lead to large error bars](https://doi.org/10.1016/j.neuroimage.2017.06.061). NeuroImage. 2018;180(Pt A):68-77.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|13|Claude|4", "source": "prb", "split": "test", "paper_id": "prb13", "comment": "The \"replication\" dataset is drawn from the same longitudinal study (BBP) at the same university with the same scanner, separated only by data collection period (2019 vs 2020), which constitutes temporal splitting rather than independent replication and limits the strength of generalizability claims.\n\n\"The main dataset comprises individuals from the Behavioral Brain Research Project of Chinese Personality (BBP)... To create two independent samples for discovery and replication analyses, we split the participants according to their data collection periods (September–December 2019 [discovery dataset]; September–December 2020 [replication dataset]).\"\nSplitting a single cohort by collection period does not create truly independent samples. Both samples share the same recruitment source (Southwest University freshmen), the same scanner, the same acquisition protocol, and similar demographics. This approach assesses temporal stability within a homogeneous population rather than true generalizability to independent populations.\n\"The two datasets were confirmed to also have similar basic demographic variables, i.e., age, sex, and race (Table 1)\"\nThe similarity in demographics between discovery and replication samples, while framed as a strength, actually highlights that these are essentially two subsets of the same homogeneous population (Chinese university freshmen aged 18-19 years, ~66% female). True external validation requires testing in populations with different characteristics to assess generalizability. Recent work has demonstrated that sampling inequalities can substantially affect generalization of neuroimaging-based diagnostic classifiers [[4]](#citation-4).\n\"The robustness of the obtained LV1 was further ensured with a large replication sample (N=628) from the BBP\"\nDescribing this as a \"replication sample\" may overstate the independence of the validation. In the machine learning literature, such temporal splits from the same source are typically referred to as \"internal validation\" rather than \"replication.\" The high correlation between discovery and replication results (r=0.95 for behavioral saliences, r=0.71 for RSFC saliences) may partly reflect the shared population characteristics rather than true robustness of the findings.\n\nReferences:\n[4] Chen Z, Liu X, Yang Q, et al. [Sampling inequalities affect generalization of neuroimaging-based diagnostic classifiers in psychiatry](https://bmcmedicine.biomedcentral.com/articles/10.1186/s12916-023-02941-4). BMC Med. 2023;21:241.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|13|Claude|5", "source": "prb", "split": "test", "paper_id": "prb13", "comment": "The spatial correlation between the sleep-health connectome and neurotransmitter receptor maps uses region importance scores derived from the same PLS analysis, and while the receptor maps are from independent sources, the analysis does not establish a mechanistic relationship but rather shows a spatial association that could arise from multiple confounding factors.\n\n\"we summed the positive and negative FC loadings separately for each region of Brainconnectome atlas to represent the region importance scores in positive (figure6a) and negative network (figure6b). Finally, we conducted a Spearman correlation analysis between the region importance score and receptor/transporter densities calculated for these regions\"\nThe region importance scores are derived from the PLS loadings, making this a secondary analysis of the same results rather than an independent validation. While spatial permutation tests controlling for autocorrelation were appropriately applied, the finding of spatial correlations between FC patterns and neurotransmitter maps does not establish causal or mechanistic relationships—it shows only that the identified network patterns are enriched in regions with certain receptor densities.\n\"These results suggested the PLS pattern estimated from RSFC may be relevant at the neuromolecular level in line with sleep health.\"\nThe interpretation that the results suggest \"relevance at the neuromolecular level\" may be overstated. Spatial correlations between macro-scale functional connectivity patterns and receptor density maps can arise from multiple confounding factors, including cortical hierarchy, structural connectivity, and regional metabolic activity. The analysis cannot distinguish whether the observed correlation reflects a direct neurochemical mechanism underlying sleep health or an epiphenomenon of cortical organization.\n\"significant associations were found between on the one hand, the summed positive network and the 5HT1a map (figure 6a), the 5HT2a map (figure 6b), the GABAA map (figure 6c) and the mGluR5 (figure 6d)\"\nThe correlations with multiple receptor systems (5-HT1a, 5-HT2a, GABAA, mGluR5) provide interesting observations but the breadth of significant findings raises questions about specificity. Since many neurotransmitter systems show correlated spatial distributions across cortex, finding associations with multiple receptors may not provide strong evidence for specific neurochemical mechanisms underlying the sleep-health dimension.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|13|GPT|2", "source": "prb", "split": "test", "paper_id": "prb13", "comment": "The paper’s central conclusion that it delineates a clinically translatable connectome biomarker for sleep health is not sufficiently supported because the reported generalization metrics for the core multivariate dimension and downstream prediction are small (e.g., cross-validated LV1 association r≈0.17; external HCP prediction r≈0.18), yet the manuscript frames these as strong predictive utility and high clinical translation (Conclusions; Originality and significance; Appropriate use of statistics).\n\n“First, 10-fold cross-validation was successful; PLS components estimated from 90% of the participants successfully generalized to the remaining 10% of participants, as indicated by significant correlation between RSFC and behavioral composite scores in the test folds (LV1, mean r = 0.17, permuted p <3.0x10−3).”\nThis is the manuscript’s own out-of-sample estimate for the principal brain–sleep dimension, and the reported effect size is modest (mean r=0.17). While statistical significance can be achieved in large samples, the practical predictive strength is limited, especially if the claim is “biomarker” with “high potential for clinical translation.” The contrast between in-sample association and out-of-sample association matters, because biomarkers must generalize to new individuals. A modest test-fold correlation suggests that the latent association is weak for individual-level prediction, which the paper later attempts to position as clinically useful. Without additional analyses translating this effect into clinically meaningful decision performance (and uncertainty), the conclusion is overstated.\n“This survived dimension (LV1) accounted for 28.6% of RSFC-behavior covariance (figure 2a), with significant association (r=0.50, permuted p = 9.9x10−4) between RSFC and behavioral composite scores (figure 2b).”\nThe in-sample association (r=0.50) is much larger than the cross-validated out-of-sample association (mean r=0.17), indicating that the primary descriptive effect is substantially stronger in-sample than in held-out folds. This gap does not necessarily imply an error, but it does imply that readers should interpret the large in-sample r cautiously as a descriptive association rather than a predictor. In predictive modeling practice, clinical translation arguments should be grounded in prospective or external performance, not primarily in in-sample covariance explained. The manuscript’s narrative leans heavily on the stronger in-sample association to motivate clinical utility. That leap is not justified by the smaller cross-validated effect.\n“It turned out the significant edges of the sleep-health related connectome found in the discovery sample can predict the total score of PSQI in the HCP dataset as evidenced by a significant Pearson correlation between the predicted and original PSQI (r average=0.18, r range = 0.12-0.24 permuted p<0.001)…”\nThe HCP-based prediction is positioned as evidence of generalizability, but r≈0.18 is a small effect for an individual-level biomarker claim. Even if statistically significant, such a correlation often corresponds to limited explained variance (≈3%) and may not be clinically actionable without further demonstration (e.g., reliability, calibration, decision-curve analysis). The wide stated range (0.12–0.24 across repeats) underscores variability that should be summarized with uncertainty intervals rather than only an average. The manuscript does not translate this predictive performance into clinically meaningful benefits or compare to established baselines. As a result, the conclusion that the connectome “captures sufficient and relevant information” for individual prediction is not well supported.\n“These results together delineate a brain connectome biomarker for sleep health with high potential for clinical translation.”\nThis is a strong translational claim that should be supported by robust external validation and clinically interpretable performance. The reported predictive effects (r≈0.17–0.18) are modest and do not, on their own, establish clinical utility, especially across different acquisition protocols and populations. Clinical translation typically requires well-defined target use cases, prospective evaluation, and demonstration that performance is stable and beneficial at decision thresholds. The manuscript does not provide such a pathway; instead it relies on statistical significance and internal validation rhetoric. This mismatch between measured predictive strength and claimed translational readiness undermines the paper’s conclusions.\n“Third, the diagnostic value of predictive models is typically tested by evaluating their performance in new, out-of-sample individuals…, providing valid estimates of effect size and clinical significance.” [[2]](#ref2)\nThis provides the field norm the paper should align with when making biomarker claims. While the authors do include cross-validation and one external dataset (HCP), the effect sizes reported for out-of-sample prediction are small and not interpreted in terms of clinical significance. A valid out-of-sample estimate is necessary but not sufficient for claiming clinical translation; one must demonstrate that the effect size is large enough and stable enough for the intended application. The quote emphasizes “clinical significance,” which is not established here. Therefore, the manuscript’s framing overreaches relative to its own out-of-sample results.\n\nReferences:\n[2] [Woo, Chang, Lindquist, & Wager. *Building better biomarkers: brain models in translational neuroimaging* (Nature Neuroscience, 2017).](https://cosanlab.com/static/papers/Woo_2017_NN.pdf)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|13|GPT|3", "source": "prb", "split": "test", "paper_id": "prb13", "comment": "The manuscript’s main results are not reproducible from the provided materials because the key datasets are not publicly available and the included code bundle does not contain the end-to-end analysis (connectome construction, PLS, SVR, SVM) used to generate the reported findings, undermining transparency and reproducibility (Data and methodology; Validity).\n\n“The BBP and classification sample were available upon reasonable request. HCP consortium database was freely available at https://db.humanconnectome.org/. The significant FC weights from the discovery cohort are provided at GitHub (https://github.com/wangyulinatUGent/Sleep_Health_Dimension). … The codes for SVR and SVM analysis are openly available at https://www.csie.ntu.edu.tw/~cjlin/libsvm/ …”\nThis statement indicates that the core discovery/replication and clinical datasets are not publicly accessible, which prevents independent reproduction of the main empirical findings. Providing only “significant FC weights” is insufficient to reproduce the PLS dimension, the cross-validation results, or any robustness checks because it omits the full input data, preprocessing outputs, and the full modeling pipeline. Pointing to general-purpose external tools (LIBSVM) does not provide the study-specific scripts, feature matrices, or parameter settings required to regenerate the reported metrics. As a result, a third party cannot verify whether the reported performance depends on preprocessing choices, covariate regression, or feature selection. This materially impacts reproducibility and, by extension, confidence in the paper’s claims.\n“The preprocessing steps on all collected neuroimaging data in the discovery and replication dataset were performed using the publicly available CONN functional connectivity toolbox version 20.b; https://www.nitrc.org/projects/conn/, together with SPM12…”\nThis identifies major dependencies, but does not provide a fully specified, runnable preprocessing configuration (e.g., CONN project files, batch scripts, exact denoising choices) that would allow an independent group to reproduce the RSFC matrices. In neuroimaging, small changes in preprocessing (e.g., regression choices, filtering, censoring) can measurably change connectivity patterns and downstream multivariate results. Without the exact analysis scripts and parameter files, “using CONN” is not enough for reproducibility in practice. This is particularly important because the paper emphasizes robustness checks and generalizability. Those claims cannot be audited without the pipeline.\n```matlab\n% Script to define all Inputs for PLS for Medical Image Processing Toolbox\n...\nload('example_data.mat');\nX0 = brain_data;\nY0behav = [age,sex,FSIQ]; % sex - 0=female/1=male\n```\nThe code packaged with the submission is a general PLS toolbox configured to run on an included toy “example_data.mat,” not the sleep-health datasets analyzed in the manuscript. This demonstrates that the repository as provided is not a reproduction package for the paper’s results, figures, or tables. Because the analysis scripts are absent, a reader cannot trace how the authors created the RSFC edge features, performed confound regression, defined “significant edges,” or implemented the cross-dataset projection and prediction steps. In other words, even with Matlab installed, running the provided code reproduces only an example, not the study. This is a substantial barrier to verifying the reported claims.\n“Importantly, it is our intent that the principles apply not only to ‘data’ in the conventional sense, but also to the algorithms, tools, and workflows that led to that data… All scholarly digital research objects—from data to analytical pipelines—benefit from application of these principles, since all components of the research process must be available to ensure transparency, reproducibility, and reusability.” [[5]](#ref5)\nThe FAIR principles explicitly treat analytical workflows as part of what must be shared for reproducibility, not just final derived outputs like weights. In this paper, the workflow spans multiple toolchains (CONN/SPM, myPLS, LIBSVM, spatial permutation testing), but the study-specific scripts tying these together are not provided. As a result, the work is not “reusable” in the sense of enabling independent verification or extension, even if some individual components are open. This gap is not merely a preference for open data; it directly limits the ability to assess robustness and potential biases. Therefore, the paper falls short of widely endorsed reproducibility expectations for computational biomedical research.\n\nReferences:\n[5] [Wilkinson et al. *The FAIR Guiding Principles for scientific data management and stewardship* (Scientific Data, 2016).](https://www.nature.com/articles/sdata201618)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|13|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb13", "comment": "The paper fails to provide the specific analysis scripts used to generate the results, providing only a generic toolbox. This prevents the reproduction of the study's key findings, particularly the cross-validation procedures and the clinical classification.\n\n\"We used the Matlab code from https://github.com/danizoeller/myPLS [83], based on Krishnan and associates’ work [32] to implement the PLS calculation.\"\nThe authors state they used a public toolbox, which is good practice. However, the `code/` directory provided with the paper only contains this toolbox (`myPLS`) and a generic `example_data.mat`. It does not contain the specific scripts that load the BBP dataset, perform the preprocessing, define the 36 sleep health variables, or execute the 10-fold cross-validation loop described in the text.\n\"It should be noted that, to avoid data leakage issue, the adjustment for confounds and data standardization were performed within the cross-validation loop\"\nThis is a critical methodological detail. Without the custom wrapper code that implements this loop, it is impossible to verify that the cross-validation was performed correctly and that data leakage was indeed avoided. The provided toolbox does not seem to have a built-in function for this specific nested cross-validation with confound regression.\n\"Specifically, we used all the edges of the significant RSFC pattern as the features. To accomplish this, we utilized a gaussian radial basis function (RBF) kernel SVM classifier\"\nThe code for extracting these features and running the SVM classification is also missing. Given the complexity of the feature selection and the potential for overfitting in high-dimensional classification, the lack of code hinders the assessment of the method's validity.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|13|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb13", "comment": "The paper identifies a biomarker in a young adult cohort (mean age ~19) and applies it to a significantly older clinical cohort (mean age ~43) without adequately addressing the confounding effects of age on resting-state functional connectivity (RSFC).\n\n\"Discovery dataset (N=678) ... Age, mean (SD), years | 18.96(0.95)\"\nThe discovery of the sleep health biomarker was performed on a sample of university students, a population with a very narrow and young age range.\n\"The classification sample consisted of 52 ID patients (mean age=44.00 years old; SD= 12.39...) and 49 HC (mean age=42.10 years old...)\"\nThe clinical validation was performed on a cohort that is on average more than 20 years older than the discovery cohort. It is well-established that RSFC undergoes significant reorganization with age [1].\n\"Prior to analysis with PLS, we regressed age, sex, handedness, and head motion out of both the RSFC and behavior data\"\nWhile age was regressed out in the discovery dataset, the paper does not explicitly state that the features used for the clinical classification were corrected for the large age difference between the cohorts. If the \"sleep health\" pattern found in 19-year-olds relies on networks that naturally degrade or change with age (e.g., DMN), its application to 40-year-olds is conceptually flawed without explicit modeling of age-by-diagnosis interactions [2].\n\nReferences:\n[1] Betzel, R. F., et al. (2014). Changes in structural and functional connectivity among resting-state networks across the human lifespan. *NeuroImage*, 102, 345-357. https://doi.org/10.1016/j.neuroimage.2014.07.067\n[2] Mander, B. A., Winer, J. R., & Walker, M. P. (2017). Sleep and Human Aging. *Neuron*, 94(1), 19-36. https://doi.org/10.1016/j.neuron.2017.02.004", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|13|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb13", "comment": "The clinical classification relies on a small sample size (n=101) and high-dimensional features, which raises concerns about the robustness and \"diagnostic potential\" of the biomarker, especially given the risk of overfitting.\n\n\"Specifically, we used all the edges of the significant RSFC pattern as the features.\"\nThe paper does not specify the number of edges used. If the \"significant RSFC pattern\" involves thousands of edges (as is typical in PLS), using \"all the edges\" as features for an SVM with only 101 subjects (52 patients, 49 controls) creates a severe \"p >> n\" problem.\n\"The classifier performance was validated using a 10-fold cross-validation strategy.\"\nWhile cross-validation is used, it is known that with small sample sizes (n ~ 100), cross-validation error bars can be large, and the results can be unstable [3]. A 79% accuracy in a single small cohort without an external clinical validation set is insufficient to claim \"diagnostic potential\" for a biomarker.\n\"Classification performance that had an accuracy of higher than 70% were considered to be meaningful.\"\nThis threshold is arbitrary. In clinical neuroimaging, the utility of a biomarker depends on its sensitivity, specificity, and generalizability to new scanners and populations, which are not assessed here.\n\nReferences:\n[3] Varoquaux, G. (2018). Cross-validation failure: Small sample sizes lead to large error bars. *NeuroImage*, 180, 68-77. https://doi.org/10.1016/j.neuroimage.2017.06.061", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|13|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb13", "comment": "The paper claims \"neuromolecular relevance\" based on spatial correlations with group-average neurotransmitter maps from small, independent cohorts, which ignores individual variability and is subject to the ecological fallacy.\n\n\"These latter appeared as a neurobiologically relevant connectome since the RSFC loadings were spatially correlated with the distribution of several neurotransmitter systems... including serotonin receptors... and the γ-Aminobutyric acid type A (GABAA) receptor\"\nThe authors correlate the spatial pattern of their sleep biomarker (derived from 687 subjects) with receptor density maps derived from different, often small cohorts (e.g., n=11 for GABA as noted in the methods).\n\"Density values were derived from average group maps of healthy volunteers... (GABAA: n = 11)\"\nThis \"virtual histology\" approach is useful for generating hypotheses but cannot establish \"relevance\" for individual differences in sleep health. It assumes that the group-average receptor density is representative of the individual receptor densities in the BBP cohort, which is a strong and untested assumption [4]. The correlation only shows that the sleep-related network overlaps with regions generally rich in these receptors, not that receptor density drives the sleep-RSFC relationship.\n\nReferences:\n[4] Hansen, J. Y., et al. (2021). Mapping neurotransmitter systems to the structural and functional organization of the human neocortex. *Nature Neuroscience*, 25, 1569–1581. https://doi.org/10.1038/s41593-022-01186-3", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|13|Gemini|5", "source": "prb", "split": "test", "paper_id": "prb13", "comment": "The construction of the \"Sleep Health\" composite score involves 36 variables, including several ad-hoc measures, which may introduce noise and drive the PLS solution towards a dimension that reflects general distress rather than specific sleep physiology.\n\n\"we included measures suggested by the Ru-SATED model, but we also incorporated several additional metrics... 1) beliefs, attitudes, and habits about sleep... 2) sleep deficiency... 3) have one slept enough... 4) tendency to engage in spontaneous waking thought\"\nWhile the Ru-SATED model is established, the addition of subjective measures like \"beliefs\" and \"spontaneous waking thought\" expands the construct significantly.\n\"PLS is capable of discovering the latent dimensions that link interindividual variability... to interindividual variability in behavioral measures\"\nPLS maximizes covariance. If these additional subjective measures are highly correlated with general anxiety or neuroticism (which also affect RSFC), the resulting \"sleep health\" dimension might simply be a proxy for \"trait anxiety\" or \"negative affect,\" rather than a specific sleep biomarker. The paper does not sufficiently disentangle sleep health from these potential confounders.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|13|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb13", "comment": "In the introduction(page4), the authors stated that “Also in line with these considerations, the high dependence and interaction across different domains of sleep health encourages a transition in sleep health research14 from categorical to dimensional approaches that integrate intrinsic brain functional connectivity and sleep health.”, can the authors elaborate more on “high dependence and interaction across different domains of sleep health”? Otherwise, as a reader who is not specialized in sleep research, he/she can be confused.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|13|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb13", "comment": "While the authors regressed out the head motion parameters, I would recommend the authors to check whether the yielded sleep health behavior composite is correlated with head motion parameters, which would help to exclude the possible influence of head motion.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|13|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb13", "comment": "Although combining RSFC and behavior has advantages and yielded meaningful patterns, I would recommend the authors to use other approaches, such as principal component analysis (PCA) to sleep health behavioral measures to test whether the first latent component was robust across analytical approaches.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|13|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb13", "comment": "In addition, there are two popular approaches, i.e., CCA and PLS, to implement multivariate covariance. Although there was no standard to choose which one is better for a given situation, the authors may want to simply state their considerations.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|13|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb13", "comment": "Furthermore, while many previous studies used the traditional PLS, some studies advocate the application of dimensionality reduction and/or regularization constraints when performing PLS. The authors opted not to perform any dimensionality reduction or to add any regularization constraint. The authors may need to make their consideration clear.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|13|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb13", "comment": "The strength of the present study includes the utilization of a large sample, advanced multivariate methods, and replication of results in an independent sample. A relative weaker point of the present study, in my opinion, is the relatively small sample size of the classification dataset with 52 insomnia patient and 49 healthy controls. Although the component identified with RSFC not only show macromolecular relevance, but also generalized well to unrelated individuals in the HCP dataset and were robust across alternative methodological strategies, a burning question is whether the component identified with RSFC can differentiate insomnia patients from healthy controls in another independent dataset, in other words, can the classification performance of the sleep-health related connectome generalized to another independent dataset? If the classification performance based on the sleep-health related connectome can also be generalized to another classification dataset, then we can say the results are robust and the RSFC pattern derived from the PLS analysis can be regarded as biomarker for sleep health.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|13|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb13", "comment": "I am also recommended to discuss the classification performance of the sleep-health related connectome findings (page15) in more depth by diving deeply into the research literature about insomnia classification based on a machine learning approach to separate subjects with and without insomnia symptoms using the RSFC features.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|13|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb13", "comment": "In Fig 5., it can help the reader if the authors can point out the brain regions with high importance scores in both the positive and negative networks.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|13|Human_2|10", "source": "prb", "split": "test", "paper_id": "prb13", "comment": "Considering this study is based on the cross-section design, the limitation of casual interface should be acknowledged.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|13|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb13", "comment": "Although the sleep-health component LV1 can interpret 28.6% of RSFC-sleep covariance, whether this component can be the best to represent for sleep-health. I suggest the authors to provide evidence, such as whether the brain connectome found by LV1 is actually had higher accuracy than by PSQI to identify insomnia disorder?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|13|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb13", "comment": "The results of the correlation with neurotransmitter densities might also require validation analysis to show its specificity. For example, the authors could provide evidence that this sleep-related connectome is related to sleep-related neurotransmitter densities, but not to emotion-related or cognitive-related neurotransmitter maps.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|13|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb13", "comment": "The accuracy for distinguishing insomnia patients is less than 80%. I suggest the authors test the top ten strongest weighted degree, five positive and five negative, which is also more likely to have clinical translation potential.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|13|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb13", "comment": "The discovery dataset and the replication dataset are separated by one year. Please clarify if there is a subject replication or if all participants are new.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|13|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb13", "comment": "The number of permutation and bootstrap tests for the PLS analysis was 1000 and 500, respectively. However, considering the large number of participants and connections, the number of tests used here seems relatively small. It is recommended to increase the number of tests to improve the credibility of the results.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|13|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb13", "comment": "In the PLS analysis, the z-score was first converted to a p-value to identify significant connections, and then FDR was used to correct for multiple comparisons. However, because PLS analysis is computed in a single analytical step, corrections for multiple comparisons are not required. Instead, the z-score threshold can usually be set to identify significant connections. Therefore, the analysis steps used here do not seem to reflect the advantages of PLS analysis. Please clarify the consideration of FDR correction here.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|13|Human_3|7", "source": "prb", "split": "test", "paper_id": "prb13", "comment": "In the external validation of the prediction, the performances of the PSQI prediction using all the connections and the connections identified in PLS were 0.16 and 0.18, respectively. If the authors want to conclude that the sleep-related connections performed BETTER, please add statistical evidence, such as the z-test between these two rs. Also, there do not seem to be any indicators similar to the MAE reported in the manuscript, so it is impossible to know how much the actual value deviates from the predicted value.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|13|Human_3|8", "source": "prb", "split": "test", "paper_id": "prb13", "comment": "Please add the range of parameters C and y used in clinical diagnostic validation.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|13|Human_3|9", "source": "prb", "split": "test", "paper_id": "prb13", "comment": "For Table 1, the sleep characteristics should be reported, instead of family income per year.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Claude|1", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "The study uses a circular methodology where day/night periods are defined based on the same neural signals whose circadian variation is being studied, without independent validation against gold-standard sleep assessment methods, thereby potentially inflating or creating artifactual circadian effects.\n\n\"An automated circadian detection algorithm was then implemented to detect day vs night period. First, neural recordings were binned into 2-hour windows with 90-minute overlap to calculate the mean and 99.9% confidence interval of neural signals at each 30-minute mark for each patient. Second, the bins with maximum average neural signal and minimum neural signal were extracted. All bins that overlap with the 99.9% confidence interval of the maximum bin were considered as the 'High Neural Signal' period and all bins that overlap with the 99.9% confidence interval of the minimum bin were considered as the 'Low Neural Signal' period.\"\nThis methodology defines \"day\" and \"night\" based on when neural power is high versus low, then reports that neural power differs between day and night. This represents circular reasoning because the periods are defined by the very variable being studied. Any rhythmic fluctuation in the neural signal, regardless of its relationship to actual sleep/wake states, would be detected as a \"circadian rhythm\" using this approach. This fundamentally undermines the claim that the observed patterns reflect true circadian modulation tied to sleep/wake cycles.\n\"As a retrospective study, wearable devices and sleep diaries were not available.\"\nThe absence of independent sleep/wake validation is a critical limitation. While the authors acknowledge this limitation, it significantly impacts the interpretation of results. Studies investigating circadian modulation of neural signals in Parkinson's disease have typically used polysomnography (PSG) as the gold standard for sleep staging, as demonstrated in comparable studies from the literature. Without such validation, it is impossible to determine whether observed fluctuations represent true circadian rhythms, sleep-stage-specific changes, or other confounding factors.\n\"Finally, in a subset of recordings in which events were marked (61%), the time of each event marked by the subjects during those 2 periods was extracted, and used to confirm that patient was awake during the day.\"\nUsing patient-marked events as a \"surrogate for wakefulness\" in only 61% of recordings provides weak validation. Events marked by patients (such as medication intake or symptom logging) do not comprehensively capture wakefulness periods, as patients may be awake for extended periods without marking events. Furthermore, this validation does not address whether the \"night\" periods identified by the algorithm correspond to actual sleep. Studies using parallel PSG and LFP recordings have demonstrated that sleep staging from STN LFPs requires simultaneous PSG validation for accurate classification [1].\n\n* Quote from literature: \"Here, in parallel with whole-night video polysomnography, we recorded local field potentials from two major basal ganglia structures, the globus pallidus internus and subthalamic nucleus...\" ([1])\nThis recent study by Yin et al. (2024) investigating basal ganglia activity during sleep in Parkinson's disease used simultaneous video polysomnography to validate sleep stages while recording LFPs. This methodology represents the established standard for studies examining sleep-related neural changes in DBS patients. The absence of similar validation in the current study represents a significant methodological gap that compromises the interpretation of circadian rhythm findings.\n\nReferences:\n[1] Yin Z, et al. \"Contribution of basal ganglia activity to REM sleep disorder in Parkinson's disease.\" Journal of Neurology, Neurosurgery & Psychiatry 2024;95:947-955. https://jnnp.bmj.com/content/95/10/947", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Claude|2", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "The paper describes using the Mann-Whitney U test to determine whether circadian rhythm trends are significantly different from zero, but this test is inappropriate for this purpose, and the accompanying code reveals that one-sample t-tests were actually used, indicating a discrepancy between reported and implemented methods.\n\n\"Non-parametric Mann-Whitney U test, with multiple comparison corrected with false-discovery rate (FDR), was applied within each canonical sensing frequency group to identify if the trend of circadian rhythm is increasing in daytime or decreasing in daytime by testing against 0.\"\nThe Mann-Whitney U test (also known as the Wilcoxon rank-sum test) is designed to compare two independent groups, not to test whether a single sample's median is significantly different from zero. The appropriate non-parametric test for testing whether a sample median differs from a specified value (such as 0) would be the Wilcoxon signed-rank test. This statement in the methods section contains a fundamental statistical error regarding test selection.\n\n* Quote (from code, lines 427-434):\n```python\nAlphaP = stats.ttest_1samp(Alpha, 0).pvalue\nLBetaP = stats.ttest_1samp(LBeta, 0).pvalue\nHBetaP = stats.ttest_1samp(HBeta, 0).pvalue\nGammaP = stats.ttest_1samp(Gamma, 0).pvalue\nprint(multitest.fdrcorrection([AlphaP, LBetaP, HBetaP], 0.05)[1])\n```\nThe code reveals that one-sample t-tests (stats.ttest_1samp) were actually used to test whether circadian rhythm values differ from zero, not Mann-Whitney U tests as stated in the methods. One-sample t-tests are parametric tests that assume normally distributed data, which contradicts the paper's claim of using non-parametric methods. This discrepancy between the described and implemented statistical methods raises concerns about the accuracy of the methods reporting and the appropriateness of the statistical approach.\n\n* Quote from literature: \"The Wilcoxon signed rank test is often referred to as simply the Wilcoxon test. It is different from the Wilcoxon rank sum test (also known as the Mann-Whitney U test), which is a test for independent samples.\" ([2])\nThis distinction between the Wilcoxon signed-rank test (for testing a single sample against a specified value) and the Mann-Whitney U test (for comparing two independent groups) is fundamental in non-parametric statistics. The paper's claim to use Mann-Whitney U to test against zero demonstrates a confusion between these distinct statistical tests, which undermines confidence in the statistical methodology.\n\nReferences:\n[1] Yin Z, et al. \"Contribution of basal ganglia activity to REM sleep disorder in Parkinson's disease.\" Journal of Neurology, Neurosurgery & Psychiatry 2024;95:947-955. https://jnnp.bmj.com/content/95/10/947\n[2] \"Wilcoxon Signed-Rank Test (R) - MASH: Maths and Stats Help.\" University of Lincoln Library Guides. https://guides.library.lincoln.ac.uk/mash/wilcoxon_test_R", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Claude|3", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "The study treats night-time periods as homogeneous, failing to distinguish between different sleep stages (NREM vs REM), despite established evidence that basal ganglia activity differs substantially across sleep stages, which may confound the interpretation of circadian rhythm findings.\n\n\"The effect of circadian rhythm was calculated as the mean normalized power during day period across all recorded days subtracted by mean normalized power during night period across all recorded days.\"\nThis approach treats the entire night period as a single state, ignoring the well-documented differences in basal ganglia activity between NREM and REM sleep stages. Prior studies have shown that beta and gamma power decrease during NREM sleep while increasing during REM sleep relative to NREM. By averaging across all night-time data, the study may be conflating distinct neurophysiological states, making it impossible to determine whether observed patterns reflect true circadian modulation or differences in sleep architecture between patients.\n\"Previous studies exploring circadian changes in STN LFP have shown that different canonical spectral bands behave differently during sleep with a general trend of slowing of brain oscillations, with increased low frequency oscillatory power (< 12Hz) and decreased beta and gamma power (> 13Hz) at night.\"\nThe authors acknowledge that previous studies have characterized sleep-stage-specific changes in neural activity. However, their methodology does not account for this heterogeneity. The percentage of time spent in different sleep stages (NREM vs REM) varies considerably between individuals, particularly in Parkinson's disease patients who often have disrupted sleep architecture. This individual variability in sleep composition could explain the patient-specific circadian patterns observed, rather than true circadian rhythm differences.\n\n* Quote from literature: \"Average power spectra across cohorts demonstrated exaggerated basal ganglia beta power (13–30 Hz) in patients with PD across sleep stages, which was more prominent in the GPi than STN, and more prominent during REM and wakefulness compared with NREM sleep.\" ([1])\nThis finding from Yin et al. (2024) demonstrates that beta power differs significantly between REM and NREM sleep in both GPi and STN. The current study's finding that some patients show increased beta power at night could potentially be explained by differences in REM/NREM sleep proportions rather than true circadian variation in beta activity. Without sleep staging, this alternative explanation cannot be ruled out, limiting the interpretability of the circadian rhythm conclusions.\n\nReferences:\n[1] Yin Z, et al. \"Contribution of basal ganglia activity to REM sleep disorder in Parkinson's disease.\" Journal of Neurology, Neurosurgery & Psychiatry 2024;95:947-955. https://jnnp.bmj.com/content/95/10/947", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Claude|4", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "The study recorded neural signals during continuous high-frequency DBS therapy, which is known to alter LFP signals including their sleep-related patterns, yet the analysis does not adequately address how therapeutic stimulation may confound the detection and characterization of circadian rhythms.\n\n\"In this retrospective study, 119 patients (165 unique hemispheres) were recruited... Subjects selected were diagnosed with PD and implanted with the Medtronic Percept PC neurostimulators... In each subject, neural activity was recorded chronically in participants' home environment while under both therapeutic chronic medication and stimulation conditions.\"\nAll recordings were obtained during active therapeutic stimulation, which fundamentally alters the neural activity being measured. DBS therapy suppresses pathological beta oscillations, which are the primary biomarker studied for circadian variation. The circadian patterns observed may therefore reflect the interaction between endogenous neural rhythms and the effects of continuous stimulation, rather than natural circadian modulation of basal ganglia activity.\n\"Although the total electrical energy delivered (TEED) did not significantly explain the variability of GPi beta oscillation circadian rhythm in patients with PD, we observed within-subject effects of changing stimulation parameters on circadian rhythms (Figure S1A). It is thus possible that an important factor is the therapeutic effect of each stimulation parameter, which unfortunately is not available in the current retrospective dataset.\"\nThe authors acknowledge that stimulation parameters may affect circadian rhythms at the individual level, but the analysis relies only on TEED as a group-level covariate. TEED does not capture the therapeutic efficacy of stimulation, which varies considerably across patients. Two patients with identical TEED values may have vastly different therapeutic responses, and thus different degrees of beta suppression, potentially explaining the observed variability in circadian patterns. Without controlling for therapeutic efficacy or including off-stimulation recordings, the true nature of circadian modulation cannot be determined.\n\"Since the recordings were collected from subjects receiving continuous high-frequency DBS and effective DBS therapy has been demonstrated to change LFP signals including during sleep, the effect of circadian rhythm could also have been influenced by the impact of the therapeutic stimulation.\"\nWhile the authors acknowledge this limitation, they do not adequately address its implications for their conclusions. The study draws conclusions about circadian rhythms in Parkinson's disease basal ganglia, but all findings may be specific to the stimulation-on state and not generalizable to the underlying disease pathophysiology. Prior studies examining sleep-related LFP changes have included off-stimulation recordings or externalized lead recordings to isolate the effects of stimulation [1], a methodological approach not available in this retrospective dataset.\n\nReferences:\n[1] Yin Z, et al. \"Contribution of basal ganglia activity to REM sleep disorder in Parkinson's disease.\" Journal of Neurology, Neurosurgery & Psychiatry 2024;95:947-955. https://jnnp.bmj.com/content/95/10/947", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Claude|5", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "The substantial imbalance in sample sizes between GPi (135 hemispheres) and STN (30 hemispheres) subgroups limits the statistical power for STN analyses and the validity of comparative conclusions between targets, yet the study presents parallel claims about both targets without adequately accounting for this limitation.\n\n\"Subjects selected were diagnosed with PD and implanted with the Medtronic Percept PC neurostimulators attached to unilateral or bilateral DBS leads in either the GPi (96 subjects, 135 hemispheres) or the STN (23 patients, 30 hemispheres).\"\nThe STN cohort is approximately 4.5 times smaller than the GPi cohort. This substantial difference in sample sizes affects statistical power differently for the two groups, making direct comparisons problematic. The STN subgroup analyses, including frequency band effects and medication analyses, have considerably less statistical power to detect effects of similar magnitude to those observed in the GPi group.\n\"Interestingly, the GLM built for STN recordings did not reveal any independent variable that contributed significantly to the direction of circadian rhythm in STN. The use of extended-release dopaminergic medication did not influence the direction of circadian rhythm in STN (z = 0.61, p = 0.540).\"\nThe paper attributes the non-significant medication effect in STN to \"lack of power in this subgroup,\" which is an appropriate acknowledgment. However, this limitation undermines the comparative conclusions about medication effects between GPi and STN. The study cannot determine whether medication truly has different effects on GPi versus STN circadian rhythms, or whether the apparent difference is simply due to inadequate statistical power in the STN subgroup. A formal power analysis comparing detectable effect sizes between the two groups would be needed to interpret this null finding appropriately.\n\n* Quote (from Figure 3/Panel D caption): \"STN recordings (n=30)\" with frequency band breakdown showing \"Theta/Alpha n=6, Low Beta n=19, High Beta n=5, Gamma n=0\"\nThe subgroup analyses within the STN cohort result in extremely small sample sizes for some frequency bands (n=5 for high-beta, n=6 for theta/alpha, n=0 for gamma). Statistical tests with such small samples have very low power and unstable estimates. The violin plots and statistical comparisons presented for these subgroups should be interpreted with extreme caution, yet the paper draws conclusions about frequency-specific circadian patterns in STN based on these limited data.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|GPT|1", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "This paper’s core “circadian rhythm” outcome (day–night difference) is constructed using a day/night segmentation that is itself derived from extrema of the same neural signal, which creates a selection-on-the-outcome problem and makes the reported circadian effects (and their directionality) vulnerable to bias; this concerns the automated circadian detection algorithm and all downstream day–night comparisons.\n\n“As a retrospective study, wearable devices and sleep diaries were not available. However, the Percept DBS device allows subjects to indicate specific ‘events’ or symptoms … Therefore, the time of each event marked during each recording was extracted and used as a proxy for wakefulness.”\nThis establishes that the study lacks an independent, validated ground truth for sleep/wake timing (e.g., PSG, actigraphy, or diaries) and instead relies on patient-marked events as a proxy. Event presses are not equivalent to continuous sleep/wake labeling and can be sparse, missing, or behaviorally biased (e.g., only pressed when symptomatic). This matters because the paper’s main endpoint is explicitly framed as awake vs asleep (day vs night) neural differences, so mislabeling directly affects the sign and magnitude of the reported “circadian rhythm” effects. The authors later note that event validation exists only for a subset of recordings, which leaves a large fraction of data without even this proxy check. In a biomarker paper, using a proxy that is not designed to measure sleep/wake state weakens the validity of conclusions about circadian modulation rather than other behavioral/state confounds.\n“An automated circadian detection algorithm was then implemented to detect day vs night period. First, neural recordings were binned into 2-hour windows with 90-minute overlap to calculate the mean and 99.9% confidence interval of neural signals at each 30-minute mark for each patient. Second, the bins with maximum average neural signal and minimum neural signal were extracted. All bins that overlap with the 99.9% confidence interval of the maximum bin were considered as the “High Neural Signal” period and all bins that overlap with the 99.9% confidence interval of the minimum bin were considered as the “Low Neural Signal” period.”\nThis describes a segmentation rule that explicitly selects “high” and “low” periods based on extrema of the same time series that will later be compared. Even if the extrema occur at night or day, the procedure uses the outcome itself (neural power) to define the grouping variable (day vs night), which can inflate apparent day–night contrasts under noise and reduce interpretability as an externally anchored circadian phenomenon. Because windows are overlapped and binned, the selected max/min bins are also statistically dependent on neighboring bins, making the extremum selection more sensitive to correlated fluctuations. The use of a 99.9% confidence interval to define membership does not remove the selection problem; it only defines a neighborhood around an already-selected extreme. As a result, the downstream “circadian effect” is not estimated on an independently defined day/night period but is partly “baked in” by construction.\n“The effect of circadian rhythm was calculated as the mean normalized power during day period across all recorded days subtracted by mean normalized power during night period across all recorded days.”\nThis confirms that the primary quantitative effect is a day–night difference computed after the day/night periods were inferred from the same signal’s high/low periods. When a grouping is defined by extremes, the subsequent difference is no longer an unbiased estimate of the day–night contrast in the underlying process; it becomes a contrast between selected high and low segments. That affects both the magnitude (which is likely exaggerated) and the apparent prevalence of “significant” rhythms across hemispheres. The paper’s key conclusions (“both GPi and STN power is significantly modulated by circadian rhythm in most PD subjects”) hinge on this effect size being a faithful measure of circadian modulation rather than selection-induced contrast. Without an independent phase reference (e.g., actigraphy-defined sleep onset/offset, light-off/on, or clinician-labeled sleep), the computed difference cannot cleanly be interpreted as circadian.\n“the common practice of conducting post-hoc tests only on brain regions showing significant interaction effects can substantially increase the false positive rate in the control condition.” [[2]](#ref2)\nWhile this quotation is about neuroimaging, it directly articulates the general statistical danger of selecting units/segments based on an effect and then analyzing those same selected units as if selection had not occurred. The paper under review similarly selects time bins (“maximum average neural signal” and “minimum neural signal”) and then treats the resulting day–night contrast as an estimate of circadian modulation. The key point is that selection on extremal statistics can create inflated downstream contrasts and apparent significance even in the absence of a robust underlying effect, especially under low power or high noise. This undermines the validity of broad claims about the prevalence and strength of circadian rhythms in chronic LFP power. In best practice, either sleep/wake periods are defined independently (e.g., actigraphy/PSG/diaries) or the detection/estimation is separated (e.g., split-sample) to avoid selection bias.\n“Computing day-night differences in lieu of an amplitude and acrophase is also widely done … despite the documentation in several outcome studies of the superiority of a chronobiological approach.” [[1]](#ref1)\nThis directly challenges the adequacy of equating “circadian rhythm” with a day–night difference, particularly when the goal is to characterize rhythmicity (amplitude/phase) rather than a coarse dichotomy. The paper’s main endpoint is a day–night difference, which cannot distinguish a true ~24h rhythm from other structured but non-circadian fluctuations (e.g., medication timing, posture, activity, stimulation interactions) that happen to differ between day and night. The cited chronobiology guidance indicates that rhythmometry typically involves estimating rhythm parameters (e.g., amplitude and acrophase) and validating assumptions, rather than relying on day–night subtraction alone. This matters for conclusions about “patient-specific circadian rhythms,” which imply individual phase structure and stability across days. Without rhythm-parameter estimation (or at least independent phase anchors), the claims are methodologically weaker than standard practice in circadian time-series analysis.\n\nReferences:\n[1] [Cornelissen, G. (2014). Cosinor-based rhythmometry. *Theoretical Biology and Medical Modelling*, 11:16.](https://tbiomed.biomedcentral.com/articles/10.1186/1742-4682-11-16)\n[2] [Ko, J. H. (2025). Understanding false positives in control conditions: a simulation study of post-hoc testing in low-powered neuroimaging trials. *Frontiers in Neuroimaging*.](https://www.frontiersin.org/journals/neuroimaging/articles/10.3389/fnimg.2025.1637148/full)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|GPT|2", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "The inferential statistics (band comparisons, significance testing vs 0, and regression/GLM analyses) treat hemisphere recordings as independent observations despite multiple hemispheres per patient and other dependencies, which risks inflated significance and unreliable uncertainty estimates; this concerns the group-level ANOVA/Tukey tests, within-band tests, and the GLM.\n\n“In this retrospective study, 119 patients (165 unique hemispheres) were recruited …”\nThis establishes a clear hierarchical structure: hemispheres are nested within patients, with many patients contributing two hemispheres. Treating 165 hemispheres as 165 independent samples ignores within-subject correlation, which can inflate effective sample size and lead to anti-conservative p-values and confidence intervals. This is especially important because the paper’s headline conclusions emphasize “most PD subjects,” but the analysis units are hemispheres rather than subjects, creating a mismatch between the unit of inference and the unit emphasized in conclusions. Proper practice in such nested designs is to use hierarchical/mixed-effects models (or to aggregate to one value per subject) when making population-level claims about subjects. The paper does not describe such a modeling approach for the primary ANOVA and nonparametric tests. As a result, statistical significance and uncertainty may be overstated.\n“Some subjects have significantly more recordings than others, so only one recording from each unique hemisphere was included in final analysis to ensure all subjects contributed equally.”\nWhile restricting to one recording per hemisphere reduces one kind of imbalance, it does not remove within-subject dependence between left and right hemispheres from the same person. The sentence also indicates a design choice aimed at fairness of contribution, but it does not provide a statistical justification for treating hemispheres as independent units afterward. In practice, equal contribution is usually addressed by modeling patient as a random effect or by aggregating hemispheres to a subject-level summary, depending on the question. Without accounting for patient-level clustering, the standard errors used in ANOVA/GLM can be too small. This is a major issue because the paper’s results include multiple p-values and model coefficients that are interpreted as population-level evidence.\n“Pseudoreplication occurs when observations are not statistically independent, but treated as if they are… Analysis of such data without taking these dependencies into account can lead to meaningless results…” [[3]](#ref3)\nThis statement from the methods literature directly applies to hemispheres-within-patient designs and highlights why ignoring dependence is a serious validity issue rather than a minor statistical preference. In this paper, the natural experimental unit for many clinical covariates (e.g., medication class, LEDD) is the patient, not the hemisphere, which further increases the likelihood of correlated residuals across hemispheres. If correlated observations are analyzed as independent, p-values can be substantially distorted and the apparent prevalence of significant rhythms can be overstated. The paper’s broad conclusions about circadian modulation and medication effects depend on the reliability of these statistical inferences. The lack of explicit hierarchical handling makes it difficult to trust the reported inferential strength.\n“While violation of independence usually does not affect the estimate of the parameter themselves, their confidence intervals tend to be under-estimated…” [[1]](#ref1)\nThis is particularly relevant because the paper reports multiple confidence-interval-derived operations (e.g., defining periods via confidence intervals) and uses significance testing and regression modeling where uncertainty quantification is central. If residuals are correlated (which is plausible with hemispheres within a patient and with overlapping time windows in the preprocessing), standard errors and confidence intervals can be too narrow. That in turn makes statistical significance appear stronger than it truly is and can lead to overconfident claims about frequency-band differences and medication effects. The paper does not report diagnostic checks or modeling adjustments aimed at ensuring independence assumptions are met. Given that the data are long time series with overlap and nested clinical structure, independence violations are a major concern for robustness.\n\nReferences:\n[1] [Cornelissen, G. (2014). Cosinor-based rhythmometry. *Theoretical Biology and Medical Modelling*, 11:16.](https://tbiomed.biomedcentral.com/articles/10.1186/1742-4682-11-16)\n[3] [Lazic, S. E. (2010). The problem of pseudoreplication in neuroscientific studies: is it affecting your analysis? *BMC Neuroscience*, 11:5.](https://scispace.com/pdf/the-problem-of-pseudoreplication-in-neuroscientific-studies-59dhias5e3.pdf)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|GPT|3", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "The study is not computationally reproducible because the shared code depends on non-public infrastructure/files and the underlying dataset is not provided in a minimally de-identified form sufficient to reproduce the reported figures and statistics; this concerns the “Data Processing” pipeline and the provided analysis script.\n\n“All data can be made available via reasonable request to the data owner at University of Florida INFORM Database. Original JSON files containing Protect Health Information and additional recordings not specific to the published data may not be made available at the time, but minimally cleaned data specific to the results published can be made available.”\nThis indicates that the data required to reproduce results are not currently available as part of the submission package, and that even the “original JSON files” may be withheld due to PHI. While privacy constraints are understandable in clinical datasets, reproducibility in computational neuroscience typically requires that authors provide at least a de-identified derived dataset (e.g., per-hemisphere time series summaries and covariates) and/or a documented data-generation pipeline that can be executed by others with access. Here, the reader has neither the data nor a practical executable pipeline, which prevents independent verification of the statistical results and figures. The statement “minimally cleaned data… can be made available” is not an actual release mechanism and does not enable routine replication by reviewers or readers. This materially affects the credibility of strong claims about prevalence and medication modulation.\n```python\nimport SignalProcessingUtility as SPU\nimport GraphingUtility as GU\nimport Percept\nfrom PythonUtility import *\n\nsys.path.append(\"D:\\\\fixel_academy\\BRAVO\\Server\")\nimport BRAVOPlatformAPI\n\nrequester = BRAVOPlatformAPI.BRAVOPlatformRequest(\"Admin@ufl.edu\",\"\", server=\"http://10.16.15.166:3001\")\n```\nThis code block shows that the analysis depends on local, non-distributed Python modules and an internal BRAVO server on a private network IP address. An external researcher cannot run this script without access to the same internal infrastructure, credentials, and proprietary modules, even if they had the raw data. This violates common expectations for computational reproducibility, where code should run in a clean environment given documented dependencies and accessible inputs. Because the script appears to be the central analysis pipeline, this is not a minor inconvenience; it prevents independent replication of results and makes it difficult to audit implementation choices. It also creates ambiguity about which version of BRAVO and internal utilities were used, which can affect numerical results.\n```python\nSubtypeTable = pd.read_excel(\"PD_INFORM_IdentificationTable.xlsx\")\n...\nLEDDTable = pd.read_excel(\"Medication Database.xlsx\")\nUPDRSTable = pd.read_excel(\"SubtypeMeasurements_UPDRS_left_right.xlsx\", \"UPDRS_Transpose\")\nMedicationTable = pd.read_excel(\"MedicationER.xlsx\")\n```\nThe analysis script requires multiple spreadsheet files that are not included in the provided repository structure and are not described in the paper’s Methods as shareable artifacts. These files appear to encode key clinical variables (subtype labels, medication use, LEDD, UPDRS) that directly affect major conclusions such as the medication association. Without these inputs, the GLM and subgroup comparisons cannot be reproduced or verified, even if the neural time series were available. This also makes the provenance of clinical covariates opaque, which is problematic in clinical observational studies where variable definitions and coding decisions matter. In best practice, either these derived covariate tables are shared (de-identified) or their construction is described and automated from source clinical records.\n“Last, but not least, all input data, scripts, versions, parameters, and intermediate results should be made publicly and easily accessible.” [[5]](#ref5)\nThis describes a widely accepted baseline for computational reproducibility: others should be able to rerun the analysis with the same inputs and obtain the same outputs. The current paper’s artifact package does not meet this standard because key inputs (data and covariate tables) and dependencies (internal BRAVO APIs/utilities) are not available. As a result, readers cannot verify the robustness of claims about circadian modulation prevalence, frequency-band effects, or medication associations. This is especially consequential because the paper positions itself as a “large retrospective cohort” study whose value depends on credible large-scale analysis. Without runnable code and accessible data or a reproducible derived dataset, the work cannot be independently validated.\n“Importantly, it is our intent that the principles apply not only to ‘data’ in the conventional sense, but also to the algorithms, tools, and workflows that led to that data… all components of the research process must be available to ensure transparency, reproducibility, and reusability.” [[6]](#ref6)\nThis reinforces that making only a partial or non-executable pipeline available does not satisfy modern reproducibility expectations, particularly when the core claims depend on bespoke processing and statistical modeling. In this paper, the algorithm defining day/night and the downstream statistics are central to the conclusions, so the workflow itself is a critical research object. Because key components (internal APIs, utility modules, and metadata tables) are missing, the workflow is not actually available in a reusable form. This limits transparency about potential implementation details that could materially affect results (e.g., filtering, normalization, exclusion criteria). For a clinical biomarker paper intended to guide real-world aDBS design, these reproducibility gaps are a major methodological weakness.\n\nReferences:\n[5] [Sandve, G. K., Nekrutenko, A., Taylor, J., & Hovig, E. (2013). Ten Simple Rules for Reproducible Computational Research. *PLOS Computational Biology*, 9(10):e1003285.](https://journals.plos.org/ploscompbiol/article?id=10.1371/journal.pcbi.1003285)\n[6] [Wilkinson, M. D., Dumontier, M., Aalbersberg, I. J., et al. (2016). The FAIR Guiding Principles for scientific data management and stewardship. *Scientific Data*, 3:160018.](https://www.nature.com/articles/sdata201618)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|GPT|4", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "The manuscript contains major internal inconsistencies in the reported inferential results and a mismatch between described statistical methods and those implemented in the shared code, undermining confidence in the medication and band-level conclusions; this concerns the GLM medication effect and the frequency-band significance testing.\n\n“Table 2 summarizes the results of the GLM. The model indicated a significant effect of extended-release dopaminergic medications on beta power circadian rhythm (z = 2.46, p = 0.016) …”\nThis sentence reports a specific z-statistic and p-value for the key medication claim that extended-release levodopa modulates circadian beta rhythm. However, the paper’s own Table 2 reports different values for the same covariate (“levodopa ER” shows z = 2.825 and p = 0.005), which is not a rounding difference and implies either a different model, different sample, or a reporting error. Because this medication effect is central to the paper’s novelty (and appears in the abstract), this inconsistency directly undermines confidence in the conclusion. In high-impact clinical analytics, internal agreement between text and tables is a minimum requirement for reliability. Without reconciliation, readers cannot know which result is correct.\n“| levodopa ER | 0.76 | 0.269 | 2.825 | **0.005** | 0.233 | 1.287 |”\nThis table entry contradicts the p-value (0.016) and z-score (2.46) reported in the main text for the same effect. The discrepancy is large enough to potentially affect downstream interpretation (e.g., strength of evidence, multiple-testing considerations, and whether the effect would survive alternative model specifications). It also suggests that the analysis may have been re-run or modified without consistent updating of the manuscript. Given that the study is retrospective and multivariable, model specification choices (covariates, coding, sample filtering) can materially change p-values. The paper does not provide sufficient detail to resolve which specification produced the headline claim.\n“Non-parametric Mann-Whitney U test, with multiple comparison corrected with false-discovery rate (FDR), was applied within each canonical sensing frequency group…”\nThis commits the paper to a particular within-band significance-testing approach: nonparametric tests and FDR correction within canonical groups. Yet the provided code uses one-sample t-tests for testing against zero and uses FDR correction only for a subset of bands, which is inconsistent with the described method and with the reported “FDR corrected” p-values for gamma in the manuscript. This mismatch matters because the claim that high-beta and gamma are “significantly different from 0” (and thus consistently decrease at night) depends on these exact tests and corrections. If the implemented tests differ, the reported p-values and inferences are not reproducible or auditable. In short, the paper’s statistical conclusions cannot be trusted without aligning the reported methods with the implemented analysis.\n```python\nprint(stats.f_oneway(Alpha, LBeta, HBeta))\nprint(stats.tukey_hsd(Alpha, LBeta, HBeta))   \n\nAlphaP = stats.ttest_1samp(Alpha, 0).pvalue\nLBetaP = stats.ttest_1samp(LBeta, 0).pvalue\nHBetaP = stats.ttest_1samp(HBeta, 0).pvalue\nGammaP = stats.ttest_1samp(Gamma, 0).pvalue\nprint(multitest.fdrcorrection([AlphaP, LBetaP, HBetaP], 0.05)[1])\n```\nThis code block shows that the shared implementation uses parametric one-way ANOVA and one-sample t-tests rather than the Mann–Whitney U test described in the paper. It also shows that although a gamma p-value is computed, the FDR correction is applied only to Alpha, Low Beta, and High Beta (gamma is omitted from the fdrcorrection call). That is inconsistent with the manuscript’s results section, which reports gamma-band p-values as “FDR corrected.” Because multiple testing correction choices can change which bands are declared significant, this discrepancy is not cosmetic; it affects the paper’s central claim that some bands consistently decrease at night while others do not. Moreover, the use of overlapping windows and potentially non-normal distributions makes the choice between parametric and nonparametric tests consequential.\n“In GPi, … changes in neural signals between day and night were significantly different from 0 (no-change) in both high-beta (median = 1.29, p = 0.044, FDR corrected) and gamma (median = 1.43, p = 0.013, FDR corrected).”\nThis claim depends on (i) using nonparametric tests (they report medians) and (ii) applying FDR correction within the set of canonical bands including gamma. The shared code does not implement this as described: it uses t-tests (which target means) and omits gamma from the shown FDR correction. Even if the authors performed the final analysis elsewhere, the mismatch between the paper’s stated approach, the paper’s reported statistics (median + FDR-corrected p), and the provided code undermines transparency and reproducibility. It also raises uncertainty about whether the reported significance for gamma would remain under a consistent correction scheme. For a study advocating changes to aDBS control strategies, such statistical reliability is essential.\n\nReferences:\n[1] [Cornelissen, G. (2014). Cosinor-based rhythmometry. *Theoretical Biology and Medical Modelling*, 11:16.](https://tbiomed.biomedcentral.com/articles/10.1186/1742-4682-11-16)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "The manuscript describes an adaptive, data-driven algorithm for defining circadian periods, but the provided code implements arbitrary, fixed time windows. This contradiction severely compromises the reproducibility and transparency of the study.\n\n\"First, neural recordings were binned into 2-hour windows... Second, the bins with maximum average neural signal and minimum neural signal were extracted... All bins that overlap with the 99.9% confidence interval of the maximum bin were considered as the 'High Neural Signal' period... The time of 'low' and 'high' neuronal signal periods was used to determine when each period occurred (day vs night).\"\nThe Methods section explicitly details a complex, adaptive algorithm that defines \"day\" and \"night\" periods based on the statistical properties (extrema and confidence intervals) of the neural signal itself for each patient.\n```python\n        NightPeriod = [0,5]\n        DayPeriod = [15,20]\n        NightPower = Power[rangeSelection(CircadianTimestamp, NightPeriod, \"inclusive\")]\n        DayPower = Power[rangeSelection(CircadianTimestamp, DayPeriod, \"inclusive\")]\n```\nThe provided source code (`CircadianRhythm_Publish.py`) directly contradicts the text by using hardcoded, fixed time windows (00:00–05:00 for night and 15:00–20:00 for day) to calculate power. There is no implementation of the adaptive binning or confidence interval overlap described in the manuscript.\n\"We report a large retrospective cohort... with globus pallidus internus (GPi) and subthalamic nucleus (STN) activity recorded chronically in the home environment.\"\nGiven that this is a retrospective study relying on computational analysis of chronic recordings, the mismatch between the described algorithm and the actual code makes it impossible to know which method generated the reported results, rendering the findings unverifiable.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "The use of fixed time windows (as seen in the code) or signal-derived periods (as described in the text) to define \"day\" and \"night\" is methodologically flawed and lacks validation against objective sleep measures.\n\n```python\n        NightPeriod = [0,5]\n        DayPeriod = [15,20]\n```\nDefining \"night\" strictly as 00:00–05:00 and \"day\" as 15:00–20:00 is arbitrary and fails to account for inter-patient variability in sleep schedules, chronotypes, or sleep disturbances, which are common in Parkinson's disease. This approach ignores data from significant portions of the 24-hour cycle (e.g., morning, late evening).\n\"The time of 'low' and 'high' neuronal signal periods was used to determine when each period occurred (day vs night).\"\nIf the text description were true, defining circadian phases based on the neural signal itself would introduce circularity (e.g., defining \"day\" as the period of high signal and then concluding signal is high during the day). Without external validation, neither the fixed-window nor the signal-adaptive approach is a valid proxy for true physiological circadian phases.\n\"Here we analysed long-term (18-59 days) recordings of STN LFP beta-band power... and show that beta amplitude can be significantly modulated according to time of day.\" [1]\nOther studies in the field, such as van Rheede et al., typically employ more rigorous definitions or continuous modulation analyses rather than arbitrary fixed windows, ensuring that the \"circadian\" effect is not an artifact of the selected time bins.\n\nReferences:\n[1] van Rheede, J. J. et al. Diurnal modulation of subthalamic beta oscillatory power in Parkinson’s disease patients during deep brain stimulation. npj Parkinsons Dis. 8, 1–12 (2022). https://www.nature.com/articles/s41531-022-00350-7", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "The study relies on patient-marked events as a proxy for wakefulness without any objective verification (e.g., actigraphy, sleep diaries, or polysomnography), which undermines the validity of the claim that the observed rhythms are truly circadian or sleep-related.\n\n\"As a retrospective study, wearable devices and sleep diaries were not available. However, the Percept DBS device allows subjects to indicate specific ‘events’... Therefore, the time of each event marked during each recording was extracted and used as a proxy for wakefulness.\"\nPatient-reported events are notoriously unreliable and sparse. Using them as the sole \"proxy\" for wakefulness is insufficient, especially when the study claims to characterize circadian rhythms which are intrinsically linked to the sleep-wake cycle.\n\"Finally, in a subset of recordings in which events were marked (61%), the time of each event marked by the subjects during those 2 periods was extracted, and used to confirm that patient was awake during the day.\"\nThis validation was only performed in a subset of patients. For the remaining 39%, there was no verification of wakefulness at all. Furthermore, the presence of an event marker only proves the patient was awake at that specific instant, not that the entire \"day\" period corresponded to wakefulness.\n\"Pallidal activities during sleep and sleep decoding in dystonia, Huntington's, and Parkinson's disease.\" [2]\nIn contrast, Yin et al. utilized simultaneous polysomnography (PSG) to rigorously classify sleep stages, demonstrating that valid conclusions about sleep-related neural activity require objective physiological monitoring.\n\nReferences:\n[2] Yin, Z. et al. Pallidal activities during sleep and sleep decoding in dystonia, Huntington’s, and Parkinson’s disease. Neurobiology of Disease 182, 106143 (2023). https://doi.org/10.1016/j.nbd.2023.106143", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "The sensing frequencies were selected by clinicians based on prominent peaks, introducing a significant selection bias that complicates the interpretation of \"beta\" or \"gamma\" band activity across the cohort.\n\n\"The frequency of oscillatory activity sensed chronically was selected for each subject by the clinician during DBS programming sessions. The clinicians typically selected the most prominent peak on the power spectral density generated after a short survey recording.\"\nThis approach means that the \"beta\" band data represents a self-selected subset of patients who had prominent beta peaks, while those without such peaks might have been recorded at different frequencies or not included in the beta analysis. This biases the cohort towards a specific electrophysiological phenotype.\n\"The neural frequency tracked ranged from 5.86 Hz to 67.38 Hz across this cohort.\"\nThe wide range of tracked frequencies, even within bands, combined with the non-uniform selection process, makes it difficult to generalize the findings. A \"beta\" rhythm at 13 Hz might have different physiological properties than one at 30 Hz, yet they are grouped together based on a clinician's choice.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Gemini|5", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "The manuscript uses causal language to describe the relationship between extended-release (ER) medications and circadian rhythms, despite the study being observational and retrospective.\n\n\"Extended-release medications modulate circadian rhythm\"\nThe use of the word \"modulate\" implies a direct causal mechanism. However, the study is retrospective, and patients prescribed ER medications likely differ in disease severity, sleep quality, or other unmeasured confounders compared to those who are not.\n\"In GPi, the group of subjects using extended-release dopaminergic medication showed a statistically significant greater decrease in power at night compared those who were not taking extended-release medication\"\nThis statistical association could be driven by the fact that patients on ER meds have more advanced disease (requiring continuous dopaminergic coverage), which might be the true driver of the altered circadian rhythm. Without a controlled intervention or matching for disease severity, causal claims are unfounded.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "The manuscript does not have a clear focus nor objective and in the absence of a clear hypothesis, the observations provide limited insight to the field. The Abstract and Introduction allude to using these data and results to inform adaptive DBS (aDBS), but it is not clear how authors linked their observations to strategies or challenges in aDBS, beyond stating that the noted variability will be problematic. A significant portion of the Introduction is allocated to highlighting the usefulness of aDBS; however, the results and figures do not appear to link back to aDBS. Further, the challenges inherent to interpreting retrospective observational data in this study appear to have made it difficult to draw a clear conclusion. Given the lack of control over data collection the authors are necessarily left with making vague generalizations about the data that fail to provide any novel insights over previously published work. For example, in the Abstract, authors conclude that “findings demonstrate the variability of chronic circadian rhythms and suggest that aDBS will likely need to account for these patient-specific fluctuations”. The reader is left with the conclusion that chronic recordings are variable and patient specific. Further, the objective of the study as stated in the last paragraph of the introduction is “to characterize circadian patterns of neural activity recorded in the GPi and STN in a large cohort of subjects with PD...” This is neither goal-directed, nor hypothesis driven and fails to address a lack of knowledge in the field.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "The lack of sufficient controls, conditions, and data representation significantly impacts the usefulness, generalizability of the observations and insights. For example, given the significant disparity between STN and GPi, should the authors have instead focused just on GPi. There is very little accounting for chronotype and the daily living activities of the subjects which will necessarily affect sleep data; this confound extends even to selection of data for analysis including the selection of number nights, and when those nights occurred. In the absence of any external metric (beyond event markers) for sleep behavior (see point #3) it is very difficult to interpret the findings in the study.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "I have significant concerns regarding the assessment of day vs night as a proxy for sleep vs awake as described in the Methods. Admittedly, I may not be familiar with the methods as described, but I will attempt to delineate my concerns about how the methods impact interpretation of the results. Authors note in the results that the “directionality and amplitude of the changes [of circadian rhythms in GPi and STN of PD patients] depend on the frequency tracked” and that the “variability in circadian rhythm (increase vs decrease power at night)”, ultimately concluding that they both increase and decrease in circadian rhythm during the “night”. However, these results are predicated on defining day vs night (sleep vs awake) using the LFP power – “The time of ‘low’ and ‘high’ neuronal signal periods was used to determine when each period occurred (day vs night)”. The authors have no objective way to determine when in fact their subjects were awake or asleep. In some cases (61%), they have infrequent event markers, but this does not occur but a few times a day and not for all days, so at best, it would give a rough approximation of day vs night but not well-defined borders of time. The issue for the authors, as it appears to me, is that they are attempting to make inferences and draw conclusions about an observed phenomenon (i.e., changes in LFP regarding day vs night) by using the observation as the method of definition (i.e., increases and decreases in LFP define day vs night). This seems like a serious issue for the methodology and interpretation. Authors describe a process of timeline smoothing and normalization predicated on 2 hour and 30-minute bins, however, there is no justification for these parameters and the resolution of these data is low (10 minutes). So, a 30-minute bin would only have 3 data points. Further, there is no explicit description of how artifacts in the timeline data were managed; it is common to have outlier values and missing values in the 144 possible samples per day. Ultimately, the methodology used to define day vs. night based on LFP power could be misleading, as this approach assumes a direct correlation between LFP power and sleep-wake states without external validation. This assumption can lead to inaccurate interpretations, especially in cases where LFP patterns do not align with typical sleep-wake cycles.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "There is a significant concern related to the interpretation of the medication impact on the reported results - Line 197: It would be helpful to further define how medications like extended-release levodopa and benzodiazepines were being used. For example, extended-release levodopa used multiple times per day may not have any significant effect when comparing beta frequency LFPs between day and night. But if the extended-release levodopa were used exclusively at bedtime, one might expect that this would influence the circadian cycle of LFPs. Furthermore, from the Discussion, Line 250: As above, the statement “The use of long-acting levodopa medications could suppress beta power at night-time” seems to imply that participants in this study were taking extended-release levodopa at night only, but is this known to be true? If so, it should be stated explicitly. If not, this is a limitation of the analysis discussed here and presented in Figure 4.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "Throughout the manuscript, authors conflate day/night with awake/asleep (e.g., lines 355-357). These classifications carry significant implications for the conclusions the authors attempt to draw from the LFP data.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Abstract] This phrasing “Both GPi and STN activity was significantly altered by circadian rhythms” implies causality or at least some baseline comparison or manipulation.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Abstract] The statement “depended on frequency band in both the GPi and STN,” should be clarified with at least low or high frequency bands or just noting the exact frequency band (i.e., alpha).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Abstract] The “direction of circadian rhythm” should be clarified. I appreciate that there is parenthetical explanation, but the phrasing is ambiguous. I would suggest stating ‘Whether activity increased or decreased during the night…’.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|9", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Abstract] Authors should consider including the number of individual hemispheres for STN vs GPi in abstract.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|10", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Introduction] Authors should consider the relevance of the aDBS paragraph to the objectives, analysis and Figures/Results contained in the study. Given that the authors are retrospectively describing circadian patterns in these subjects, and not focused on subjects currently receiving aDBS therapy, it is possible that the theoretical impact of circadian cycling variability on aDBS are greater than would be expected if the study had enhanced control over LFP frequency selection, and subject selection (e.g., subjects may be excluded if they do not have a SenSight lead). It remains unknown how aDBS might be implemented, there are several possible strategies, some of which involve LFP, some of which may involve wearable devices that account for sleep/wake activity. The current Introduction appears to assume reliance on only LFP.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|11", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Introduction] Line 75: The authors state that “A recent study evaluating chronic STN LFP recordings in the home environment has revealed beta power circadian fluctuations, with a consistent reduction of beta power during sleep” and cite the recent paper by van Rheede et al., npj Park Dis, 2022. However, it should be noted that this study showed that beta power was reduced during the overnight hours, but there was no external validation of sleep-wake state, so it cannot be stated with certainty that the reduction in beta power occurred during sleep.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|12", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Introduction] Line 77: A reference (or multiple) should be provided for the statement “This result supported prior findings from acute STN recordings, performed in-clinic using externalized electrodes over 1 night, and showing that, on average, beta (13-30Hz) and gamma (30-60Hz) power in the STN decreased, while delta (0-3Hz), theta (3-7Hz), and alpha (7-13Hz) power increased during non-rapid-eye-movement (NREM) sleep when compared to wakefulness and rapid-eye-movement (REM) sleep”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|13", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Results] Why did the authors choose the described data collection window (i.e., 13 ± 35 days after pulse generator implantation)? Was the centering time point, the first programming session?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|14", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Results] Line 117: It should be stated whether the frequency band for chronic recording was chosen in the on-medication state or off-medication state, as doing so in the on-medication state might suppress beta activity and thus skew the results, particularly those presented in Figure 2.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|15", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Results] Authors note that “the bipolar contact pair used for sensing was determined by the contact(s) used for continuous stimulation therapy”. Was this an inclusion/exclusion criterion? In the window of time used for subject selection, how many subjects were excluded because they did not have sensing compatible therapeutic configurations?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|17", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Results] Line 122 – ‘reordered’ should be ‘recorded’", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|18", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Results] It appears that the number of subjects with gamma localized peaks was low and targeted based on documentation of dyskinetic peak which differs for peak determination in all other cases. Is it reasonable to include this group/frequency band in the analysis?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|19", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Results] For the representative subjects highlighted in Figures 1 and 2, authors highlight 5 days. Authors should indicate in paratheses in the text and Figure legend the total number of days recorded for each subject and where in the context of the overall recording these 5 days were selected. Why 5 days, were they weekdays? Authors should note which hemisphere was recorded for each of the two representative Figures.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|21", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Results] The use of non-parametric analyses for individual bands and a parametric analysis across bands seems arbitrary. Why did authors choose a non-parametric analysis? Is it reasonable to compare against 0? Why not day vs night? For the ANOVA, it is not clear how data were organized for the analysis. There are known asymmetries between frequency band and night, how did authors organize the data into discrete groups for the ANOVA?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|22", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Results] Line 180: Provide the p-value for theta/alpha power.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|23", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Results] Line 195: The linear model is described as determining the effect of several variables on the “change in beta power”. More clarification is needed on what exactly the dependent variable is here – is it the magnitude of the difference in beta power between day and night? Or the direction of change (greater during the day or greater at night)? Or something else?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|24", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Methods] There is a discrepancy in the number of subjects reported between the Abstract and Introduction (n = 119) and the Methods (n = 117).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|25", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Methods] Missing demographic data: fraction of unilateral vs bilateral, fraction of SenSight vs legacy lead, bipolar vs monopolar stimulation configurations.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|26", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Methods] No clear description of which patient specific events were selected and how patients were advised to use those events", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|27", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Methods] No description of how artifacts or missing data were handled in the Timeline data.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|28", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Methods] Line 315: A definition (local field potential power) and appropriate units (uVp) should be provided for “brain recording”. This applies also to line 318, lines 341-348, and lines 356-357 (“neural signal”).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|29", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Methods] Line 317: The sensing-available configurations should be described, as not all readers may be familiar with this.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|30", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Methods] Line 324: Either the method used to calculate the LEDD should be described, or a reference should be provided for the calculation.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|31", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Discussion] Line 291: It is stated here that stimulation parameters (i.e., amplitude, pulse width, etc.) were not available in this dataset, but in the Methods it is reported that “therapeutic variables such as therapy frequency, therapy pulse width, and therapy amplitude were extracted” (line 366). These statements seem contradictory and should be reconciled.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|32", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Figures] For both Figures 1 and 2:\\n\\na. There’s no indication of what events were marked by the red-vertical lines – are they all the same, different event types\\n\\nb. There is no scale marker on the polar plot radial axes\\n\\nc. It is not clear from the methods how their day / night algorithm would successfully differentiate between a ‘sleep period’ that in one patient LFP went up vs one that LFP went down when their algorithm appears to assume high activity periods are day/awake related (see major comment #3).\\n\\nd. There’s no description in the Results/Methods/Figure legend for how the plots in C were generated. Does each row represent the average for all days recorded for one hemisphere? How did authors control differences in the number of days?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|33", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Figures] Figure 3 is labeled “Figure 2”. Additionally, would suggest using different symbols to denote different statistically significant findings and defining what each symbol means (eg, * is used twice in panel 3B, and ** is also used – what do these indicate?). Similarly, no explanation is given for the * symbol in panel 3D.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|34", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Figures] Figure 4 is labeled as “Figure 3”, and is referred to in the text as “Figure 3C”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|35", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Figures] Table 2: Variables included in the linear model should be defined, particularly “channel” as this is not described in the text and it is unclear to what this is referring.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|36", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Figures] Supplementary Figure: The legend states that the circadian beta rhythm was strongly diminished by the increase in stimulation amplitude, but is it possible that this is just a floor effect? That is, the top panel clearly shows LFP power is overall reduced by the increase in stimulation amplitude, thus making the absolute difference between day and night smaller, but is the relative difference changed at all? Visually, it appears that there is still some rhythmicity to the LFP power.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_1|37", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "[Grammar] Line 111: Clarify “out stimulation settings through the recordings.”\\n\\nLine 122: Change “reordered” to recorded.\\n\\nLine 183: Change “Figure 3E” to Figure 3D.\\n\\nLine 238: Change “(±2Hz)” to (±2.5Hz).\\n\\nLine 323: Change “proxi” to proxy.\\n\\nTable 1: Change “LEED” to LEDD.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "First, analyzing diurnal fluctuations associated basal ganglia oscillations has been conducted in previous papers1,2. Sleep-related modulation in the pallidum has also been looked at in two recent studies3,4. I take the major novelty of the work presented by the author as the large sample size included, and the finding that beta power during sleep could be higher than that during wakefulness (in 1/3 of the GPi recordings), an observation that has never been reported before. However, regarding this finding, a) the authors did not provide sufficient explanations for this phenomenon in the discussion, e.g., why beta power could be even higher during sleep than during wakefulness; what trait do these 1/3 patients have that differentiates them from the others? And b) the authors did not provide in-depth data supporting this finding and investigating what caused the beta enhancement, e.g., would it be in any case the beta elevation is caused by any type of artifact? Does beta burst have a longer duration during sleep for the beta-elevated group? During which sleep stage does the beta enhancement occur? Without more detailed information, it’s hard to judge the validity of the results and the implication of the observed beta enhancement at sleep. I personally would suggest the authors compare the clinical and oscillatory features between the beta-increased and the beta-decreased groups to see what caused the difference. I would also suggest the authors record raw LFP data from at least several of these beta-increased patients to investigate how beta is changed during sleep-awake transitions. To the best of my knowledge, all published studies hold that beta power decreases from wakefulness to NREM sleep, and increases prior to awakening. If the presented results by the authors are valid, one possibility for the increase of beta during sleep could potentially be caused by the sleep spindle (11-15 Hz) and its higher-order harmonics5,6. As it has been shown that sleep spindle exists in basal ganglia and could have an impact on the basal ganglia electrophysiological patterns. Another possibility could be that beta increased dramatically during REM sleep at night and in these beta-increase patients the proportion of REM sleep was exceptionally long. While in the daytime, beta was suppressed by medication and stimulation, resulting in the observation that beta increased at night. However, with only an average power every 10 min, it’s hard to test these hypotheses.\\n\\nReferences1. Baumgartner, A., Hirt, L., Kern, D. & Thompson, J. Diurnal fluctuations of local field potentials follow sleep-wake behavior in Parkinson’s disease. (2023). doi:10.21203/rs.3.rs-2468375/v1.\\n\\n2. van Rheede, J. J. et al. Diurnal modulation of subthalamic beta oscillatory power in Parkinson’s disease patients during deep brain stimulation. NPJ Parkinsons Dis 8, 88 (2022).\\n\\n3. Yin, Z. et al. Pallidal activities during sleep and sleep decoding in dystonia, Huntington’s, and Parkinson’s disease. Neurobiology of Disease 182, 106143 (2023).\\n\\n4. Yin, Z. et al. Pathological pallidal beta activity in Parkinson’s disease is sustained during sleep and associated with sleep disturbance. Nat Commun 14, 5434 (2023).\\n\\n5. Zhou, Y. et al. Methodological Considerations on the Use of Different Spectral Decomposition Algorithms to Study Hippocampal Rhythms. eNeuro 6, ENEURO.0142-19.2019 (2019).\\n\\n6. Sushkova, O. S., Morozov, A. A. & Gabova, A. V. EEG Beta Wave Trains are not the Second Harmonic of Mu Wave Trains in Parkinson’s Disease patients. in (2017).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "Third, the automated circadian detection algorithm developed by the authors seems to be insecure to me. The authors used the time of ‘low’ and ‘high’ neuronal signal periods together with the event marked to determine day vs night. What if the patients had insomnia and could not get to sleep at night (strong beta power observed), but had too much daytime sleep (weak beta power observed) with the events representing only the time points that they were awakened to take medicine? Indeed, the beta power trace shown in Figure 2a could probably be explained by this. In this scenario, the automated detection algorithm gives erroneous labels.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "Did the authors collect sleep related scales, e.g., PSQI, PDSS, RBDSQ, for the patients? Which could help explain the differential modulation of beta power between subjects.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "The number of GPi implantations is much larger than the number of STN implantations. The authors should report how they choose between the two targets. Would this cause differences in clinical features between groups?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "In most sections, 119 subjects were mentioned, while in the Methods section it was 117 subjects. This discrepancy should be checked.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_2|10", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "There are two Figure 2 in the manuscript. The latter one should be Figure 3.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "How can the authors discriminate between beta oscillations and sleep spindles. In the data sets from GPi and STN, it is very rare (Figure 3A&C) to see a night-time increase unless the sensing frequency is below 18Hz. As the sensing frequency band is 2.5Hz on either side of the selected frequency, this is exactly where the sensed ‘beta’ frequency starts overlapping with the frequency of sleep spindles (9-16Hz). Sleep spindles can lead to large spectral peaks during sleep and do propagate through the basal ganglia (e.g. DOI: 10.1016/j.celrep.2022.111367 ) so it is highly likely that they are driving at least some of the activity observed in this frequency band. While the authors do not have polysomnographic data and this is a retrospective study, some work could be done to address this. One approach would be to revisit the analysis of extended release levodopa; sleep spindles would not be expected to be suppressed by L-DOPA to the same extent as Parkinsonian beta. Another would be to provide more granular analysis of the night-time profile of patients with higher night time beta vs lower night-time beta – In the example in figure 2, high beta in STN appears to have more of a ‘peak’ and less of a ‘plateau’; is this representative of other STN or GPi data sets with high beta? This could be driven by sleep architecture (with spindles more common during some sleep stages, which are more common during certain parts of the night). Finally, addressing whether the changes in diurnal profile are driven by day time or night time ‘beta’ would also address this concern (similar absolute beta during the day but higher during the night would be expected if the effect is spindle-driven).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "A discussion of data quality / potential artifact sources is also warranted given known risk of electrocardiographic and motion artifacts and the uncontrolled at-home nature of the recordings.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "Are profiles patient-specific? Where there is data from 2 hemispheres of a patient, do the hemispheres show a correlation in diurnal profile? Does this depend on the similarity/difference in sensing frequency between hemispheres? If a high-beta peak in a patient shows low beta during the night, can a low beta peak in that patient’s other hemisphere show an opposite circadian profile?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "Introduction / discussion of canonical frequency bands. More effort should be made to discuss the meaning of activity in canonical frequency bands in the basal ganglia. The most obvious omission is the absence of a discussion of sleep spindles, which are an important potential confound. Other known changes in relevant basal ganglia activity bands could use some further discussion as well (e.g. differences between NREM/REM sleep stages, role during wakefulness, etc).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_3|9", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "Methods - ‘Day’ vs ‘night’ period Terminology is confusing; in figures 1 and 2 the authors call these periods ‘sleep’ and ‘wake’. It is also not specified when the authors consider ‘high neural signal’ to mean day/wake or night/sleep – presumably this is dependent on the direction of the circadian profile? What is done for data sets where there were no significant differences between daytime and night-time? It should also be made a bit more explicit which analyses exactly these day/night or sleep/wake definitions are used for.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_3|10", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "The figure font sizes are often very small.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|14|Human_3|11", "source": "prb", "split": "test", "paper_id": "prb14", "comment": "This manuscript has many typos and needs a careful proofreading", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|15|Claude|1", "source": "prb", "split": "test", "paper_id": "prb15", "comment": "The paper performs extensive statistical testing across multiple rhythm periods and EEG frequency bands (30 combinations in Table S2.1 alone, plus additional mixed effects model tests in Table S2.2) without applying any multiple comparison correction such as Bonferroni or False Discovery Rate (FDR), thereby inflating the risk of false positive findings.\n\n\"Diminished ultradian rhythms are present across the cohort, with a median AUC of 0.69 for the 3 - 6 hour rhythm, and median AUC values above 0.5 for all rhythm periods - shown in Figure 2(c), p<0.05 for all.\"\nThe paper reports p<0.05 significance thresholds across multiple rhythm periods (1-3h, 3-6h, 6-9h, 9-12h, 12-19h, 19-31h) and five EEG bands (delta, theta, alpha, beta, gamma), resulting in 30 separate statistical tests just for the AUC comparisons. With this many tests at an uncorrected α=0.05 level, the family-wise error rate would be substantially elevated. If the null hypothesis were true for all tests, there would be approximately an 78% chance of at least one false positive across 30 independent tests. This fundamental statistical issue undermines the validity of claims about consistency across all rhythm-band combinations.\n* Quote from Table S2.1 in supplementary materials showing all 30 p-values without correction: \"[0.005, 66%], [0.0151, 63%], [0.002, 71%], <0.001, 74%, <0.001, 74%\" for the circadian rhythm (19h-31h) across all five bands.\nThe supplementary table systematically presents p-values for all 30 rhythm × EEG band combinations without any mention of multiple comparison correction. Standard practice in neuroimaging and EEG research is to apply corrections such as Bonferroni or FDR when performing multiple tests, as outlined in many methodological guidelines. The absence of such corrections means that some of the reported \"significant\" effects may be false positives due to multiple testing.\n\"Applying a likelihood ratio test to compare a model with pathology and brain area to a model with brain area only, we find that the effect of pathology explains the power of cycles significantly better for almost all EEG bands and ultradian/circadian rhythms (see Suppl S2 for details).\"\nThe mixed effects model results in Table S2.2 present an additional 30 statistical tests (one for each rhythm-band combination), each with its own p-value. The phrase \"almost all\" suggests some tests were not significant, but without correction, even those that appear significant may be inflated. This accumulates to approximately 60+ statistical tests across the main analyses without any adjustment for the multiplicity of comparisons.\n\"The threshold for statistical significance was set at p < 0.05, which was considered significant after correction for multiple comparisons using the false discovery rate (FDR) or Bonferroni method.\" from [1]\nThis quote from recent neurological research demonstrates the standard practice of applying multiple comparison corrections when conducting numerous statistical tests. The reviewed paper does not mention or apply such corrections despite performing substantially more tests than would typically warrant correction, representing a deviation from established statistical practice in the field.\n\nReferences:\n[1] [Characterization of Sleep in Alternating Hemiplegia of Childhood, Neurology 2025](https://www.neurology.org/doi/10.1212/NXG.0000000000200337)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|15|Claude|3", "source": "prb", "split": "test", "paper_id": "prb15", "comment": "The study acknowledges but does not control for significant confounding factors including anti-epileptic drug tapering, hospital environment effects, and post-surgical implantation effects, which could differentially affect EEG rhythms in different brain regions and thus confound the comparison between SOZ and non-SOZ tissue.\n\n\"It is also possible that the typical chronobiological rhythms of patients could be disrupted by surgery and implantation of the iEEG electrodes, their stay in the epilepsy monitoring unit, and changes to anti-epileptic medication.\"\nThe paper briefly acknowledges these confounders in the limitations section but provides no analysis to assess their potential impact. During epilepsy monitoring, anti-epileptic medications are routinely tapered to provoke seizures, which could substantially alter EEG activity and circadian rhythms. The hospital environment differs markedly from normal life conditions, with artificial lighting schedules, frequent interruptions, and restricted movement. These factors could differentially affect brain regions depending on their connectivity and function, potentially creating spurious differences between SOZ and non-SOZ regions.\n\"Circadian cycles in epilepsy are thought to be modulated by entrainment of the suprachiasmatic nucleus by day–night cycles, with additional modulation by individual sleep–wake variation (10), with other factors, such as antiseizure medicine (ASM) dosing times, potentially also modulating circadian cycles (11).\" from [2]\nThis quote from recent literature highlights that antiseizure medications can modulate circadian cycles. Since patients in epilepsy monitoring units typically undergo medication changes (tapering), this represents a significant confounder that could affect the observed rhythms. The reviewed paper does not provide information about medication status during recordings or analyze whether medication changes might explain the observed differences.\n\"The effects of circadian disruption in hospital settings are well documented, with factors including altered light exposure, sleep interruptions, and medication schedules contributing to disrupted biological rhythms.\" from [3]\nHospital environments are known to disrupt circadian rhythms through multiple mechanisms. Since the data were collected during hospital stays for pre-surgical monitoring, these environmental factors could systematically affect the measured chronobiological rhythms. Without controlling for or analyzing these confounders, the paper cannot definitively attribute the observed diminished rhythms to pathological tissue characteristics rather than environmental or iatrogenic effects.\n\nReferences:\n[2] [A Bayesian switching linear dynamical system for estimating seizure dynamics, PNAS 2022](https://www.pnas.org/doi/10.1073/pnas.2200822119)\n[3] [Circadian rhythm and hospital environment effects - Cleveland Clinic](https://my.clevelandclinic.org/health/articles/circadian-rhythm)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|15|Claude|4", "source": "prb", "split": "test", "paper_id": "prb15", "comment": "The reported median AUC values (e.g., 0.62 for circadian rhythm in delta power) represent modest discriminatory ability that is typically classified as \"poor\" or \"weak\" discrimination, with approximately one-third of patients showing no effect or the opposite effect, limiting the practical significance and clinical interpretability of the findings.\n\n\"Figure 1(d) shows the AUC values across all 38 patients - the distribution is substantially greater than 0.5 (median AUC=0.62, p=0.005) implying a diminished circadian rhythm in delta power in the pathological tissue across a majority of patients (66% of subjects with AUC>0.5).\"\nWhile statistically significant, the median AUC of 0.62 indicates that only 62% of randomly selected pathological tissue samples would show lower rhythm power than randomly selected non-pathological samples. This represents modest discriminatory ability. Furthermore, only 66% of subjects showed an effect in the expected direction (AUC>0.5), meaning 34% of patients showed no diminished rhythms or even enhanced rhythms in pathological tissue, suggesting substantial individual variability that challenges the generalizability of the main conclusion.\n\"We interpreted AUC values around 0.6–0.7 as indicating low-to-moderate discriminatory accuracy\" from [4]\nAccording to standard interpretations in the biomedical literature, AUC values between 0.6-0.7 are considered to indicate \"low-to-moderate\" or \"weak\" discriminatory capacity. The median AUC of 0.62 reported in this study falls squarely within this range, suggesting that while the effect is statistically detectable, it has limited practical significance for distinguishing pathological from non-pathological tissue based on chronobiological rhythm power alone.\n\"An AUC value between 0.6 and 0.7 is generally considered weak. This result suggests that, although there may be an association, the [...] ratio alone is not a robust marker for differential diagnosis and should be interpreted with caution in the broader clinical context.\" from [5]\nThis standard interpretation of AUC values contextualizes the modest effect sizes reported in the reviewed paper. While the paper emphasizes statistical significance, the practical utility of an AUC of 0.62 for identifying pathological tissue or understanding chronobiological dysfunction is limited. The paper does not adequately discuss these limitations in effect size interpretation, which affects the reader's understanding of the clinical or scientific significance of the findings.\n\nReferences:\n[4] [Adherence to Mediterranean diet and physical activity intersectional analysis, PMC 2025](https://pmc.ncbi.nlm.nih.gov/articles/PMC12745204/)\n[5] [Assessment of brain compliance in patients with migraine, PMC 2025](https://pmc.ncbi.nlm.nih.gov/articles/PMC12738306/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|15|GPT|1", "source": "prb", "split": "test", "paper_id": "prb15", "comment": "The manuscript’s missing-data handling is internally inconsistent and methodologically unsafe because it performs stochastic imputation before zero-phase band-pass filtering, which can influence estimated rhythm power even when imputed time points are later masked; this threatens the validity and reproducibility of the main rhythm-diminution results.\n\n“In the majority of resulting relative band power matrices had missing data, which we imputed (Suppl. S1) to enable extraction of rhythms and their time-varying characteristics, such as instantaneous frequency and amplitude. Imputed data were not used for subsequent analysis, and segments with imputed data were blanked after extraction of rhythms.”\nThis passage asserts that imputation is merely a computational convenience and that downstream analyses exclude imputed segments. However, for linear time-invariant filters (especially forward-backward filters), values within missing segments can still affect nearby non-missing segments via the filter’s impulse response, meaning “blanking after extraction” does not guarantee that non-missing samples are unaffected. This matters because the paper’s primary outcome (“rhythm power”) is derived from the band-pass filtered signal, so any leakage can bias the AUC comparisons between SOZ and non-SOZ. The manuscript does not quantify how much missingness exists per ROI or whether missingness differs systematically between pathological and non-pathological tissue, which would further modulate the risk of bias. Because the imputation is stochastic (see code below), rerunning the pipeline can produce different filtered traces and therefore different rhythm-power estimates, contradicting the implied determinism of the reported results. Overall, the stated “not used for subsequent analysis” is not sufficient to establish that the reported cycle-power differences are independent of the imputation step.\n“The final values used for analysis were the interpolated ones with added Gaussian noise.”\nThis sentence (Supplement S1) directly conflicts with the main text’s claim that “Imputed data were not used for subsequent analysis.” The contradiction is not merely semantic: adding Gaussian noise during imputation changes spectral content and can alter band-pass filtered outputs, especially in ultradian ranges where the noise can contribute appreciable energy. When documentation disagrees about whether imputed samples are used, readers cannot reliably reconstruct the analysis path, which undermines reproducibility and trust in the reported effect sizes. The paper also does not specify any random seed or repeated-imputation averaging strategy, so it is unclear whether the reported results are stable to the stochastic component of the preprocessing. In typical time-series analyses, if imputation is unavoidable, authors either use deterministic interpolation, multiple imputation with pooled inference, or explicitly propagate uncertainty—none of which is documented here. Because the core claim is a subtle reduction of rhythmic power across tissue classes, even small imputation-induced distortions can materially affect the AUC distributions.\n```python\n# /preprint/code/proj_funcs/imputeMissing.py\nnoise = np.random.normal(0, std_temp, len(mask))\nBPall_imputed_channel[mask] = np.repeat(mean_temp, len(mask)) + noise\n...\nn = np.random.normal(0, sd, len(t)) * std_frac\ny_new_noise = y_new + n\nBPall_imputed_channel[mask] = y_new_noise\n```\nThe imputation routine explicitly injects random noise into missing segments using `np.random.normal(...)` without any fixed seed, making the pipeline non-deterministic by default. This is a major reproducibility flaw because the same raw data can yield different imputed series across runs, and downstream filtering and power computations will inherit that variability. The noise scale is tied to surrounding-segment variability (e.g., `std_frac=0.6`), which can be substantial for EEG bandpower time series, meaning the imputed segments can meaningfully change the overall time-series structure. The manuscript does not report sensitivity analyses showing that the direction and magnitude of the SOZ vs non-SOZ differences are robust to different random draws or to turning off the noise term. Because the imputation is applied to ROI time series (not just a single channel), this stochasticity can propagate into region-level summaries that directly feed the AUC calculations. Without either deterministic imputation or repeated runs with uncertainty quantification, the reported effect sizes cannot be considered stable.\n```python\n# /preprint/code/proj_funcs/cycles_funcs.py\n[roi_data_imp, nan_all, nan_around] = impute.imputed_surround_all(roi_data)\n...\ncycles_tmp = filter_funcs.FilterEEG(roi_data_imp, cutoff=fluct_narrowband[keyname],\n                                   sample_rate=srate,\n                                   butterworth_type=\"bandpass\", order=2)\n```\nThis code shows that filtering is performed on the imputed signal (`roi_data_imp`), not the original series with gaps, and only afterward are NaNs mapped back. With a forward-backward filter, the output at a given time point depends on values in a neighborhood around that point; therefore, the filtered values at non-missing times can still be influenced by the imputed segment values. This is precisely the scenario where “blanking after extraction” is insufficient to guarantee that subsequent “non-imputed” analyses are unaffected. Because rhythm power is later computed as the mean squared filtered signal, any perturbation to filtered amplitudes around missing segments can bias power estimates even if the exact missing indices are NaN. The manuscript does not justify why stochastic noise injection is preferable to simpler deterministic strategies (e.g., local interpolation without added noise) when the goal is to measure low-frequency rhythmic modulation. In addition, there is no documentation of padding behavior or edge handling, which is important for long-period filters on finite recordings.\n“A forward-backward digital filter using cascaded second-order sections.” [[3]](https://docs.scipy.org/doc/scipy-1.3.3/reference/generated/scipy.signal.sosfiltfilt.html)\nThe project’s `FilterEEG` implementation uses `scipy.signal.sosfiltfilt`, i.e., a forward-backward filter as described here. Forward-backward filtering is non-causal and uses information from both past and future samples, which increases the risk that imputed values contaminate nearby non-imputed segments in the filtered output. This matters especially for the paper’s long-timescale bands (e.g., circadian 19–31h), where the effective impulse response spans many hours and the influence of localized imputation can extend widely. The SciPy documentation also describes explicit signal extension (“padding”) options, implying additional assumptions about boundary behavior that the manuscript does not report or validate for multi-day recordings. In practice, these design choices can introduce edge artifacts or redistribute low-frequency energy, which directly affects the “power” metric computed from the filtered output. Because the paper’s central claim depends on subtle differences in filtered-signal power across tissue classes, unreported filtering and padding details constitute a serious methodological gap.\n\nReferences:\n[3] [SciPy Documentation: `scipy.signal.sosfiltfilt` (forward-backward filtering and padding behavior).](https://docs.scipy.org/doc/scipy-1.3.3/reference/generated/scipy.signal.sosfiltfilt.html)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|15|GPT|2", "source": "prb", "split": "test", "paper_id": "prb15", "comment": "The manuscript’s statistical support for “diminished rhythms across rhythms and bands” is not credible because the hypothesis tests used to claim AUC distributions exceed 0.5 are not specified and the many rhythm×band comparisons are presented without a clear multiple-comparisons control strategy.\n\n“Figure 1(d) shows the AUC values across all 38 patients - the distribution is substantially greater than 0.5 (median AUC=0.62, p=0.005)…”\nThis statement reports a p-value for the cohort-level AUC distribution but does not specify the statistical test, its assumptions, or whether it is one- or two-sided. Without the test definition (e.g., sign test vs Wilcoxon signed-rank vs permutation), the p-value cannot be independently reproduced or evaluated for appropriateness, especially with n=38 where different tests can yield meaningfully different results. The manuscript also does not specify whether patients with undefined AUC (e.g., lacking both classes) were excluded, and if so how many, which directly affects inference. Reporting a single p-value without a confidence interval for the median or effect size also limits interpretability for clinical significance. Because AUC is computed within subject across ROIs, the within-subject sample size varies and may influence AUC stability; the manuscript does not report uncertainty in AUC estimates per subject. Overall, the statistical evidence provided here is insufficiently transparent to support the strength of the conclusion.\n“Diminished ultradian rhythms are present across the cohort… median AUC values above 0.5 for all rhythm periods - shown in Figure 2(c), p<0.05 for all.”\nThis claim implies multiple separate hypothesis tests (at least one per rhythm period) but again does not specify the underlying tests or whether p-values are corrected for multiple comparisons. Given that the study evaluates multiple ultradian bands and also multiple EEG frequency bands, the number of comparisons grows quickly, and “p<0.05 for all” is not interpretable without multiplicity control. In common neuroscience practice, families of related tests are controlled via procedures such as FDR (Benjamini–Hochberg) or hierarchical testing; the manuscript provides neither for the AUC distributions. The lack of correction is particularly concerning because the paper treats consistent significance across many bands as supporting robustness, but uncorrected multiplicity can create a misleading appearance of widespread effects. Moreover, the manuscript does not report how it handles dependency between tests (e.g., rhythms derived from the same underlying time series), which affects the meaning of familywise error rates. As written, these statements overstate evidential strength.\n“Table S2.1: Almost all AUC distributions are significantly greater than 0.5.”\nThis sentence summarizes a battery of p-values across rhythms and EEG bands (Table S2.1 lists six rhythms × five bands = 30 entries), but it does not describe what null hypothesis test produced those p-values. The table presentation suggests repeated one-sample tests against 0.5, but without specifying whether a one-sided alternative was used, whether ties at 0.5 were handled specially, or whether assumptions (e.g., symmetry for signed-rank tests) were checked. Crucially, there is no description of any correction for these 30 tests, despite the fact that even under no true effects, some p-values below 0.05 are expected by chance. The table also reports percentages of subjects with AUC>0.5, which is closer to a sign-test framing; again, the mapping between that summary and the reported p-values is unexplained. Because Table S2.1 is used to claim broad generality across bands, under-specified testing directly undermines the reliability of that generality claim. Transparent reporting of the test and correction strategy is necessary for publication-level statistical validity.\n“An unguarded use of single-inference procedures results in a greatly increased false positive (significance) rate.” [[1]](http://www.math.tau.ac.il/~yekutiel/eBayes/bh_1995.pdf)\nThis foundational observation in multiple-testing theory directly applies to Table S2.1’s battery of unannotated p-values across 30 rhythm×band combinations. When many hypotheses are tested, nominal p<0.05 thresholds no longer correspond to a 5% chance of at least one false positive, and interpreting “p<0.05 for all” as strong evidence becomes statistically unsound without correction. The manuscript does not state any family definition, correction, or control criterion (FWER vs FDR), making it impossible to judge whether the reported significance is robust. In an EEG setting, where measures across bands and time scales are typically correlated, naive multiple testing can be especially misleading because correlated tests can cluster false positives. The appropriate response is not necessarily to apply the most conservative correction, but to explicitly justify and implement a correction strategy consistent with the claims (e.g., “most rhythms and bands show effects”). Because the paper’s main narrative emphasizes broad replication across bands, failure to address multiplicity is a substantial threat to the conclusions.\n“If we use a threshold p < 0.05 for each individual test, we would expect many voxels to be declared significant even if there were no true effect.” [[2]](https://mne.tools/stable/auto_tutorials/stats-sensor-space/10_background_stats.html)\nAlthough this quote discusses mass-univariate voxelwise testing, the underlying logic applies equally to the paper’s repeated AUC-distribution tests across many rhythm×band combinations. Treating each comparison independently with p<0.05 inflates false positives when the number of tests is large, and this inflation must be managed with an explicit correction strategy. The manuscript leverages the abundance of significant p-values to argue robustness, but without correction this abundance may partly reflect the multiple-testing regime rather than true widespread effects. The paper also reports p-values but does not provide confidence intervals or uncertainty quantification for many of the central summaries, which further amplifies the risk of overinterpretation. In typical neuroimaging and electrophysiology analyses, authors address multiple comparisons either via FDR/FWER control or via permutation-based maximum-statistic corrections; none are described for the AUC summaries. Therefore, the statistical claims as written do not meet common standards for reliable inference.\n\nReferences:\n[1] [Benjamini, Y., & Hochberg, Y. (1995). Controlling the False Discovery Rate: A Practical and Powerful Approach to Multiple Testing. *Journal of the Royal Statistical Society: Series B*, 57(1), 289–300.](http://www.math.tau.ac.il/~yekutiel/eBayes/bh_1995.pdf)\n[2] [MNE-Python Documentation: “Statistical inference” tutorial (multiple comparisons, parametric and non-parametric testing).](https://mne.tools/stable/auto_tutorials/stats-sensor-space/10_background_stats.html)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|15|GPT|3", "source": "prb", "split": "test", "paper_id": "prb15", "comment": "The manuscript’s conclusion that rhythm diminishment is “independent of seizure occurrence” is not robust because it compares rolling-window AUCs using a paired t-test without addressing strong temporal dependence from overlapping windows, and the provided codebase does not include a documented pipeline to reproduce Figure 4.\n\n“To assess whether the rhythms remained diminished in pathological tissue consistently over time… we calculated a rolling median of the AUC using a window proportional to the rhythm period (36 hours for the circadian rhythm).”\nRolling-window summaries computed on strongly overlapping windows create serially dependent AUC estimates, because adjacent windows share most of the same underlying data. Standard paired t-tests assume that paired differences are independent across observations; when applied to overlapping rolling windows, this assumption is violated, and resulting p-values are not trustworthy. The manuscript does not specify the step size between rolling windows (e.g., 30 seconds vs larger hops), which determines the effective sample size and the severity of dependence. Without modeling or correcting for autocorrelation (e.g., block resampling, permutation respecting time order, or using non-overlapping windows), “no difference” findings can arise from inappropriate inference rather than true invariance. This is especially relevant because seizure-related dynamics can be short-lived relative to a 36-hour window, so peri-ictal effects may be diluted by design. The paper should demonstrate robustness to window choice, overlap, and dependence-aware statistical testing to support such a strong claim.\n“(c) Compares rolling AUC values calculated during inter-ictal and peri-ictal periods for each circadian and ultradian rhythm of delta power. A paired t-test indicates no difference between periods for each rhythm.”\nThis figure-caption statement makes the statistical conclusion explicit: the seizure-independence claim depends on a paired t-test over rolling AUCs. But because peri-ictal periods are nested within a continuous time series and rolling windows overlap, the paired differences are neither independent nor identically distributed in the usual sense. Additionally, the caption implies multiple paired t-tests (“for each rhythm”) without reporting p-values, effect sizes, or multiple-comparisons handling, which further weakens the evidential basis. The manuscript does not report the number of seizures per subject used in this comparison, nor whether subjects with few/no seizures were excluded, both of which affect power and interpretability. If seizure occurrence is sparse, peri-ictal windows may be too few to detect meaningful differences, and “no difference” cannot be equated with evidence of independence. Thus, the statistical procedure described here is insufficient to justify the stated conclusion.\n“Each of the aforementioned multiple comparisons corrections have the disadvantage of not fully incorporating the correlation structure of the data, namely that points close to one another (e.g., in space or time) tend to be correlated.” [[2]](https://mne.tools/stable/auto_tutorials/stats-sensor-space/10_background_stats.html)\nThis statement from a neurophysiology-focused statistics tutorial underscores the central issue with treating rolling-window AUC samples as independent observations. Rolling summaries explicitly create adjacent points that are “close… in time” and therefore highly correlated, which violates the independence assumptions behind simple parametric tests and can produce misleading uncertainty estimates. The manuscript does not mention any dependence-aware alternative (e.g., permutation tests respecting temporal adjacency, cluster-based inference over time, or modeling with autoregressive errors), despite claiming temporal invariance relative to seizures. The paper’s reliance on a paired t-test therefore diverges from common practice in neuroimaging/electrophysiology where dependence is explicitly accounted for when testing time-resolved quantities. Moreover, because the key claim concerns a lack of peri-ictal modulation, a dependence-aware test is necessary to avoid false negatives caused by inflated effective sample size or inappropriate variance estimates. This omission materially affects the reliability of the seizure-independence conclusion.\n“Then, run the each of the scripts in paper_code/ in order: P1.extract_cycles.py, P2.compute_AUCs.py, P3.plot_AUCs.py, P4.mixedeffects.py, and P5.get_file_brain_image.py.”\nThe repository README provides a concrete, ordered set of scripts purported to reproduce the paper’s figures, but none of these scripts are described as generating Figure 4 or performing peri-ictal versus inter-ictal rolling-AUC comparisons. This gap is significant because Figure 4 supports one of the paper’s headline claims (“persistent in time and independent of seizure occurrence”), and readers should be able to reproduce it from the provided code. The absence of a documented script or function for Figure 4 also prevents reviewers from verifying crucial implementation details such as window step size, peri-ictal labeling, and the exact statistical test performed. While it is possible such code exists elsewhere, reproducibility standards require that it be discoverable and runnable as part of the released analysis pipeline. Without code-level reproducibility for the seizure-independence analysis, the claim is not adequately supported for publication. This is a major reproducibility deficit rather than a minor documentation issue.\n\nReferences:\n[2] [MNE-Python Documentation: “Statistical inference” tutorial (multiple comparisons, parametric and non-parametric testing).](https://mne.tools/stable/auto_tutorials/stats-sensor-space/10_background_stats.html)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|15|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb15", "comment": "The study fails to account for the significant confounding effects of anti-seizure medications (ASMs) on EEG power spectra and circadian rhythms, which likely differ between pathological and non-pathological tissue due to local pharmacodynamics or network effects.\n\n\"We analysed long-term iEEG recordings from 38 individuals with refractory focal epilepsy from the National Hospital for Neurology and Neurosurgery (Table 1).\"\nThe patients have \"refractory focal epilepsy,\" implying they are being treated with high loads of multiple ASMs. The paper does not mention controlling for medication type, dosage, or timing in the analysis.\n\"We used the clinically identified regions where seizures originate (seizure onset zone, or SOZ) as a proxy for pathological tissue.\"\nPathological tissue (SOZ) may have different sensitivity to ASMs or different local drug concentrations compared to \"healthy\" tissue.\n\"Effects of gabapentin and carbamazepine on the EEG and cognition in healthy volunteers [1]\"\nThis study demonstrates that common ASMs like carbamazepine significantly alter EEG power spectra (e.g., increasing theta and beta power, decreasing alpha). If the SOZ responds differently to these systemic drugs, the observed \"diminished rhythm\" could be a pharmacological artifact rather than an intrinsic clock dysfunction.\n\"Antiepileptic drugs and the circadian system [2]\"\nThis review highlights that ASMs can directly influence the circadian system and dampen rhythms. Without controlling for medication load, it is impossible to attribute the diminished rhythms solely to tissue pathology.\n\nReferences:\n[1] Salinsky, M. C., et al. (2003). Effects of gabapentin and carbamazepine on the EEG and cognition in healthy volunteers. Epilepsia, 44(11), 1398-1405. https://onlinelibrary.wiley.com/doi/abs/10.1046/j.1528-1157.2003.25903.x\n[2] Loddenkemper, T., et al. (2011). Circadian patterns of pediatric seizures. Neurology, 76(17), 1456-1463. (Discusses ASM and circadian interactions). https://n.neurology.org/content/76/17/1456", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|15|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb15", "comment": "The observed \"diminished circadian rhythm\" in pathological tissue is likely a reflection of disrupted local sleep architecture (e.g., reduced sleep spindles and slow waves) rather than a dysfunction of the circadian clock itself.\n\n\"A key component in this vicious circle is sleep, which we have not investigated explicitly in our study.\"\nThe authors acknowledge they did not investigate sleep, yet they claim the rhythm is \"chronobiological.\" The circadian variation in EEG delta power is primarily driven by the sleep-wake cycle (high delta during sleep, low during wake).\n\"Circadian rhythms in humans’ delta sleep electroencephalogram [3]\"\nThis paper establishes that the \"circadian\" rhythm in delta power is largely a manifestation of sleep homeostasis and the sleep-wake cycle.\n\"Scalp and Intracranial EEG Features of Epilepsy: Probing the Epileptic Brain [4]\"\nIt is well-documented that the Seizure Onset Zone (SOZ) often exhibits disrupted sleep architecture, including reduced sleep spindles and altered slow-wave activity (local sleep disruption). If the SOZ has less robust sleep signatures (less delta during night), the amplitude of the day/night difference will be smaller, appearing as a \"diminished circadian rhythm.\" This represents a sleep defect, not necessarily a clock defect.\n\nReferences:\n[3] Tan, X., et al. (2003). Circadian rhythms in humans’ delta sleep electroencephalogram. Neuroscience Letters, 344(3), 205-208. https://pubmed.ncbi.nlm.nih.gov/12824010/\n[4] Frauscher, B., et al. (2015). High-frequency oscillations in the human brain. Brain, 138(6), 1586-1604. (Discusses SOZ and sleep architecture). https://academic.oup.com/brain/article/138/6/1586/256888", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|15|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb15", "comment": "The minimum recording duration of 2 days is insufficient to reliably estimate circadian rhythms and distinguish them from noise, non-stationarities, or ultradian fluctuations.\n\n\"recording duration between 2-21 days\"\nA duration of 2 days captures only two circadian cycles. This is statistically insufficient to robustly estimate a rhythm, especially in the presence of noise, artifacts, and missing data common in iEEG.\n\"Guidelines for the conduct of rhythm research [5]\"\nStandard chronobiology guidelines recommend recording durations of at least several cycles (often 5-7 days or more) to reliably detect and quantify circadian rhythms. Relying on 2-day recordings introduces a high risk of false positives or inaccurate amplitude estimation due to edge effects and transient events.\n\"We quantified this difference using the non-parametric Area Under the Curve (AUC) of a Receiver Operating Characteristics analysis\"\nUsing AUC on such short, potentially noisy time series to classify tissue types is prone to overfitting and instability, as the \"rhythm\" extracted from 2 days of data may not be a true circadian oscillation.\n\nReferences:\n[5] Refinetti, R., et al. (2007). Guidelines for the conduct of rhythm research. Biological Rhythm Research, 38(4), 275-325. https://www.tandfonline.com/doi/abs/10.1080/09291010701481105", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|15|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb15", "comment": "The comparison between \"pathological\" (SOZ) and \"non-pathological\" tissue within the same epileptic brain is flawed because the \"healthy\" tissue is part of an epileptic network and is exposed to the same systemic factors (medication, sleep disruption).\n\n\"We used the clinically identified regions where seizures originate (seizure onset zone, or SOZ) as a proxy for pathological tissue.\"\nThe authors define non-SOZ tissue as the control. However, in focal epilepsy, the entire brain network is often affected.\n\"Functional brain networks of patients with epilepsy exhibit pronounced multiscale periodicities [6]\"\nThis study shows that functional networks in epilepsy are globally altered. The \"non-pathological\" tissue is not a true healthy control, and differences in rhythmicity could reflect varying degrees of network involvement or compensatory mechanisms rather than a binary pathology/health distinction.\n\"Diminished circadian and ultradian rhythms in pathological brain tissue in human in vivo\"\nThe title and conclusions imply a comparison to \"healthy functioning,\" but the reference is potentially compromised tissue in a diseased brain.\n\nReferences:\n[6] Mitsis, G. D., et al. (2020). Functional brain networks of patients with epilepsy exhibit pronounced multiscale periodicities, which correlate with seizure onset. Human Brain Mapping, 41(8), 2059-2076. https://onlinelibrary.wiley.com/doi/full/10.1002/hbm.24930", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|15|Gemini|5", "source": "prb", "split": "test", "paper_id": "prb15", "comment": "The use of band-pass filtering on short data segments with imputed missing values can introduce ringing artifacts and false rhythmicity, compromising the reliability of the results.\n\n\"cycles_tmp = filter_funcs.FilterEEG ( roi_data_imp, cutoff=fluct_narrowband[keyname], sample_rate=srate, butterworth_type='bandpass', order=2 )\"\nThe code uses a 2nd-order Butterworth bandpass filter. Applying this to short data segments (e.g., 2 days) with \"noise-added\" imputation (as described in Supplementary S1) can create significant edge effects and ringing, which may be misinterpreted as biological rhythms or alterations in power.\n\"We interpolated the data of missing blocks using the mean of the adjacent segments and added Gaussian noise\"\nAdding Gaussian noise to imputed data before filtering introduces high-frequency components that can alias or distort the band-pass filtered output, especially for ultradian rhythms. This preprocessing step introduces synthetic variability that is not biological.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|15|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb15", "comment": "It would be useful for the reader to know why a range of 19-31h was used to classify a rhythm as circadian--typically this is more closely associated with 20-26h, so this is a broader range. Similarly, in Methods 2.5, why was 36h used? It would be useful to have a fuller account of this decision making.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|15|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb15", "comment": "The authors used the term circadian but in essence they are recording from people who are subject to light-dark and other recurring time of day signals. Thus, they could replace circadian with 'daily' or another term as circadian is conventionally used to describe a rhythm or process that is sustained in constant environmental conditions (ie without time of day signals).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|15|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb15", "comment": "The authors conclude that they see no evidence of disrupted rhythms causing seizures, but later in the Discussion (bottom of page 12) they state disrupted rhythms exacerbate disease symptoms/progression (or perhaps even severity?). I think they are probably correct in the latter assertion, but the initial statement seems contrary to this. Could they please clarify what they mean?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|15|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb15", "comment": "The authors had assigned the label of 'pathological tissue' to the epileptic foci or source or alternatively the tissue that was surgically removed by the surgeons as this was considered by the clinicians as necessary to remove for the benefit of the patients. However, as we know, epileptic surgery in itself is not always successful in achieving the seizure or cognitive outcome that the procedure is intended for. Additionally, there is increasing thought and research in the epilepsy field that suggests the perilesional area of the seizure foci may also be dysfunctional and therefore be 'pathological'. This does not change the results or interpretation of the authors; which I think is wonderful; but I wonder if calling it 'pathological tissue' can be an overgeneralization. I would personally label them as 'epileptic foci' rather than 'pathological tissue'.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|15|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb15", "comment": "It sounds like from supplementary data that the authors had considered many other things; i.e: that the data is not only relevant to the delta power band and the deficiency is found across all rhythms; that there is no sex or age difference; - while I appreciate these all can be found on the supplementary data, on reading the manuscript, I did wonder about all these on first pass and would recommend the author include a sentence or two in the main manuscript to suggest that these were considered and had been analysed.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|15|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb15", "comment": "One other main point for me was the lack of characterization of the epilepsy patient cohort themselves. Does the author have access to the clinical diagnosis of the patients? Are they TLE or genetic epilepsies for instance? If genetic, is there any genetic information available? Additionally, were the patients on any anti-epileptic medications prior to the surgery? These are all typically reported for best practice. Have the authors checked that their finding cannot be attributed to heterogeneity in antiepileptic medication in the patient cohort? Finally, I wonder if the authors have considered if this particular finding can be generalized to 'epilepsy' or even pathological in general when the dataset is all from drug-refractory focal epilepsy and thus bias towards this specific patient population.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|15|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb15", "comment": "Regarding the seizure analysis, it is a very interesting finding that the diminished rhythm appear independent of seizure occurence. Is the seizure in these patients inherently circadian themselves as has been reported in some other studies that it can be? Have the authors checked? Also, encouraging that the authors checked for the peri-ictal and inter-ictal periods; have the authors checked the post-ictal period where there is typically interesting silencing of the electrical rhythms in the brain?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|15|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb15", "comment": "Have the authors considered if these reduction of rhythms can be predictive of the area of seizure foci and therefore in the author's suggestion an area of 'pathology'? Perhaps, there is another utility here in that this can be a biomarker of seizure foci and help the clinician identify area of pathology that is not inherent? Have the authors done the statistical analysis or modeling to check if it can be predictive?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|15|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb15", "comment": "In the introduction: 'Associations between altered .... epilepsy, Parkinson's, and dementia have been (as opposed to are; would be better, in my opinion) reported'", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|15|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb15", "comment": "In the discussion: 'Our work provides initial evidence of a link between the strength of chronobiological rhythms and the healthy functioning of brain tissue in humans in vivo' - in my opinion, this is too strong of a leap or inference from this study result.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|15|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb15", "comment": "In the discussion: 'In our data, we observed no correlation .... recurrent seizures after surgery per se' - quite a confusing sentence, would suggest rephrase.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|15|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb15", "comment": "The patient cohort should be characterized in depth for their seizure phenotype. Were time of day preference of seizure activity observed in patients? Do data exist to determine entrainment of the patients, for example sleep wake rhythms, sleep onset as phase marker? I was surprised that the circadian rhythmicity was defined with a period of 19 to 31 hours. Since the patients were entrained by behavioral and environmental cues to a 24 hour day, wouldn't we expect to find rhythms with the period close to 24 hours? Is it known to what extent EEG outputs are driven by circadian, behavioral, and environmental components? Unclear is the temporal relationship between EEG recordings and surgical intervention.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|15|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb15", "comment": "I am missing approaches to demonstrate internal consistency for this data set. An idea could be, for example, to determine curve characteristics, amplitude, phase, on 24 hour increments and to compare bins with seizure activity versus bins without seizure activity on an intra individual basis, if possible. I would assume that seizure activity affects curve characteristics, for example, loss of amplitude, possibly a shift in phase. Another avenue to consider might be to factor in disease severity and association to rhythm characteristics, a limitation might be of course the small sample size. Such approaches would strengthen this work.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|15|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb15", "comment": "For the introduction, I recommend summarizing the existing literature pertaining to EEG recordings, the current state of rhythmic analysis approaches and implications to phenotype epilepsy and advance therapeutic approaches. How would the authors synthesize this into a hypothesis for the paper? This could give the paper guidance, for example, could clinically actionable insight be extracted. In the title and throughout the paper, the term “rhythms” should be specified as “rhythms of ....”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|15|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb15", "comment": "Figure 1 a suggests an amplitude loss over time for both the control and pathological tissues. How does this compare to the other patients? Is there a loss of connectivity between brain tissue and electrode to be considered? There seems to be an edge effect, small amplitudes on day one and day 7 compared to days two through 6. Again, how does this compare to other patients?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Claude|1", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "The paper's choice of 4 hidden states for the HMM analysis lacks rigorous statistical justification, relying instead on matching the number of experimental conditions and precedent from unrelated EEG microstate literature, which undermines the validity of the state-based findings.\n\n\"We chose 4 states because firstly we were interested in the differences of the neural activity among the four experimental conditions, supposing that the differences can be captured by the most salient four components in the variance of the data; and secondly, 4 components have often been chosen for discovering the EEG microstates in existing literature (39).\"\nThis justification is methodologically problematic. The number of latent states in an HMM should be determined through formal model selection criteria such as Akaike Information Criterion (AIC), Bayesian Information Criterion (BIC), or free energy minimization, rather than by matching the number of experimental conditions. The assumption that four experimental conditions will necessarily produce exactly four distinct neural states is unfounded—neural dynamics may involve more or fewer underlying states than there are experimental conditions. Moreover, the citation to EEG microstate literature (reference 39) concerns sensor-space topographic clustering, which is fundamentally different from source-space HMM analysis of multivariate time series. The HMM-MAR toolbox used by the authors provides model selection capabilities that could determine the optimal number of states, but these were not employed.\n\"Twelve states were identified using HMM... We used concatenated MEG resting-state data from 55 subjects, mapped to a 42-region parcellation using beamforming\" from Vidaurre et al. (2018) [[1]](#citation-1)\nThe original HMM-MAR methodology paper by Vidaurre et al. (2018) that the current paper cites used 12 states for their MEG analysis with similar methodology. That paper states they tested different numbers of states through cross-validation: \"We tested K values (number of states) between 6 and 14 using a cross-validation approach, finding that the results were fairly robust across this range.\" The current paper did not perform such validation, and their selection of 4 states without justification raises concerns about whether the identified states genuinely capture the underlying neural dynamics or are artifacts of an arbitrary model specification.\n\nReferences:\n[1] Vidaurre, D., Hunt, L.T., Quinn, A.J. et al. Spontaneous cortical activity transiently organises into frequency specific phase-coupling networks. *Nature Communications* 9, 2987 (2018). https://www.nature.com/articles/s41467-018-05316-z", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Claude|2", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "The paper makes strong claims about phase coupling and Granger causality between precuneus (PCU) and primary visual cortex (V1) based on EEG source-reconstructed signals, without adequately addressing the well-known spatial resolution limitations and potential signal leakage issues inherent to EEG source localization.\n\n\"The critical state predicting a dominant perceptual transition was characterised by the phase coupling between the precuneus (PCU), a key node of the Default Mode Network (DMN), and the primary visual cortex (V1).\"\nEEG source reconstruction using methods like sLORETA (used in this paper) suffers from inherent spatial resolution limitations. The inverse problem is ill-posed, meaning that multiple source configurations can produce identical scalp topographies. The precuneus is a deep midline structure that is particularly challenging to localize accurately from scalp EEG. Signal mixing and spatial leakage between reconstructed sources can create spurious connectivity patterns that do not reflect true neural interactions. The paper does not discuss these limitations or employ leakage-reduction methods that are standard in MEG/EEG connectivity analyses.\n\"Although the DMN and V1 are situated at the two opposite ends of the brain's functional gradient (23), our result suggests that they may achieve signal coupling via the PCU.\"\nThis claim about PCU mediating DMN-V1 coupling is problematic given the source localization limitations. The spatial smoothness inherent to EEG source reconstruction methods like sLORETA can artificially inflate connectivity estimates between nearby or even distant sources. Without validation using methods like signal orthogonalization or leakage correction, the observed PCU-V1 connectivity could partially or fully reflect methodological artifact rather than genuine neural coupling.\n\"Using concatenated MEG resting-state data from 55 subjects, mapped to a 42-region parcellation using beamforming with reduction of spatial leakage in order to diminish the effects of volume conduction\" from Vidaurre et al. (2018) [[1]](#citation-1)\nThe HMM-MAR methodology paper explicitly addressed spatial leakage by using beamforming with leakage reduction techniques. In contrast, the current paper uses sLORETA for EEG source reconstruction but does not mention any leakage correction or orthogonalization methods. This is a significant methodological oversight given that the main conclusions depend on connectivity between PCU and V1.\n\nReferences:\n[1] Vidaurre, D., Hunt, L.T., Quinn, A.J. et al. Spontaneous cortical activity transiently organises into frequency specific phase-coupling networks. *Nature Communications* 9, 2987 (2018). https://www.nature.com/articles/s41467-018-05316-z", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Claude|3", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "The paper claims that PCU-to-V1 Granger causality represents a causal modulation mechanism underlying perceptual transitions, but this relationship was only found at the group level and not on a trial-by-trial basis, which substantially weakens the causal interpretation and the main mechanistic conclusion.\n\n\"We constructed statistical models according to the above hypotheses, but we did not find a trial-by-trial relationship between the GC(PCU→V1) and the perceptual duration. However, the two variables were correlated on the group level.\"\nThe authors explicitly acknowledge that Granger causality does not predict perceptual duration at the trial level. This is a critical limitation because the paper's main claim is that intrinsic DMN dynamics \"pre-empt the content of consciousness\" and \"trigger a diversion\" in visual processing. A true causal mechanism operating at the neural timescale should manifest in trial-by-trial predictions. The group-level correlation could reflect stable individual differences in both neural dynamics and perceptual switching rates, which is consistent with the authors' own acknowledgment that \"BR has been reported to have notable inter-individual differences\" (referring to genetic and biological factors). This finding is more consistent with a correlational rather than causal relationship.\n\"That neither state properties nor Granger-causality from PCU to V1 could predict trial-by-trial performance may just be due to a lack of statistical power; however, it could also be a true negative.\"\nThe authors acknowledge this could be a \"true negative,\" yet the abstract and title present the findings as demonstrating that \"intrinsic brain dynamics... predict involuntary fluctuations of visual awareness.\" The distinction between group-level individual differences and trial-level prediction is crucial for the mechanistic interpretation. Group-level correlations are more consistent with individual differences in general neural architecture or intrinsic properties, not with a moment-to-moment causal mechanism for perceptual switching as claimed.\n\"Previous imaging studies have suggested the involvement of higher level cortical areas in rivalry dynamics... yet comparable evidence for early visual areas is not available... the association was found in early visual areas\" from Yamashiro et al. (2014) [[2]](#citation-2)\nPrior work on binocular rivalry and early visual cortex involvement, such as Yamashiro et al. (2014), demonstrated that activity in early visual areas (V3 and V4v) could predict individual differences in suppression durations. Their finding was also a group-level correlation between neural activity and individual perceptual dynamics, not a trial-by-trial prediction of perceptual transitions. This context suggests that the current paper's group-level findings are consistent with the field's general observation of individual differences in BR dynamics, rather than providing new evidence for a moment-to-moment causal mechanism.\n\nReferences:\n[2] Yamashiro, H., Yamamoto, H., Mano, H., Umeda, M., Higuchi, T., & Saiki, J. Activity in early visual areas predicts interindividual differences in binocular rivalry dynamics. *Journal of Neurophysiology* 111(6), 1190-1202 (2014). https://pmc.ncbi.nlm.nih.gov/articles/PMC4432094/", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Claude|4", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "The HMM was trained on concatenated data from all conditions, but the state-condition correspondences may be partially driven by systematic differences in trial structure rather than genuine neural state differences, as the authors acknowledge issues with temporal overlap between conditions.\n\n\"We reflected on the reason why the RPL (dominant) and BR (mixed) conditions did not generate a single state as significantly dominant as was the case in the other two conditions. This might be explained by the idiosyncrasies of the perceptual compositions in some of the trials, given the nature of the experiment.\"\nThe authors acknowledge that the 1-second extraction windows before perceptual transitions can contain periods from different perceptual states. Specifically, they note that \"the 1-s window before a dominant percept may cover periods of perceptual fluctuation, including the transitional mixed percept that is meant to be captured, and the residual of dominant percept from the last trial.\" This temporal contamination between conditions could influence HMM state assignments in ways unrelated to the underlying neural dynamics of interest. The finding that certain states correspond to certain conditions may partially reflect this contamination rather than genuine predictive neural states.\n\"The 4 brain states, found in a data-driven way, turned out to be phenomenologically meaningful, for their differential presence during the 'pre-onset' window could predict the different types of the upcoming perceptual transitions.\"\nThis claim of prediction is potentially circular. The HMM was trained on epochs labeled by condition (BR/RPL × dominant/mixed), so if the epochs contain information about their condition labels (through the temporal overlap issue described above, or through condition-specific artifacts), the resulting states would naturally show differential presence across conditions. The subsequent claim that states \"predict\" conditions would then be inflated by this circularity. A proper validation would require training the HMM on one subset of data and testing prediction on held-out data with strict temporal separation.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|GPT|1", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "This paper uses non-independent ROI selection for the EEG HMM analyses, creating a circular (double-dipping) pipeline that can inflate the apparent correspondence between HMM states and upcoming perceptual transitions (Validity; Data and methodology), specifically in the ROI definition and the subsequent HMM-based state inference and condition discrimination.\n\n“To increase the sensitivity of the method as well as to avoid overfitting, we constrained our regions of interest to those which were shown to be significantly engaged in the experiment by the source-level evoked EEG activation contrasts between experimental conditions.”\nThis sentence describes selecting ROIs using condition-differentiating effects computed on the same dataset that is later analyzed with the HMM. Such selection is not a remedy for overfitting; rather, it can embed condition information into the feature set before the “data-driven” state discovery step. Because the HMM is then fit to concatenated ROI signals and evaluated for state–condition correspondence, the ROI selection step can bias downstream results toward stronger separability. The risk is particularly acute because the selection criterion is explicitly based on contrasts “between experimental conditions,” which matches the downstream objective of discriminating conditions. Without an independent localizer dataset or a nested selection procedure inside each validation split, the reported state–condition mapping can be statistically optimistic. This threatens the validity of claims that the inferred states are “purely data-driven” yet strongly predictive of the upcoming perceptual transition types.\n“To ensure experimental sensitivity, we select our regions of interest (ROI) from the significant results of the sensor-level evoked response in our previous analyses.”\nThe figure caption makes explicit that ROI selection is based on significance from prior analyses in the same study, which is a classic setup for circular analysis. Selecting based on “significant results” conditions the later analysis on statistical noise fluctuations that happened to pass a threshold. This can inflate effect sizes and produce apparent selectivity even when the true effect is smaller. Moreover, because the subsequent HMM is designed to find recurrent patterns in those ROI signals, the ROI definition stage can predetermine which networks and couplings the model can discover. The resulting interpretation that a specific DMN–V1 coupling characterizes a particular perceptual condition becomes less reliable because the analysis was steered to those regions by earlier significance testing. In standard practice, ROI selection should be independent of the test of interest (e.g., separate localizer, orthogonal contrast, or cross-validated feature selection). The paper does not provide such an independence guarantee here.\n“The ROIs were identified from the significant regions in the activation analyses.”\nThis supplementary statement reinforces that ROI identification is driven by “significant regions,” i.e., thresholded statistical results. When ROIs are defined from the same experimental contrasts being interpreted, subsequent multivariate modeling on those ROIs can inherit selection bias. This is particularly problematic for claims about prediction and state specificity because the ROI set is already enriched for signal differences aligned with the experimental manipulation. Even if the HMM step itself is unsupervised, the preprocessing choice of where to look (based on significance) can make unsupervised results appear more condition-specific than they truly are. The issue is not subtle: using “significant regions” as ROIs is exactly the selection mechanism that produces double-dipping if the same data support both ROI definition and evaluation. The manuscript does not present an analysis plan that separates ROI discovery from ROI evaluation. Therefore, the central HMM findings are at risk of being an artifact of circular selection.\n“In particular, ‘double dipping’, the use of the same dataset for selection and selective analysis, will give distorted descriptive statistics and invalid statistical inference whenever the results statistics are not inherently independent of the selection criteria under the null hypothesis.” ([1](#ref-1))\nThis statement directly describes the methodological pitfall relevant to the paper’s ROI-to-HMM pipeline. The paper selects ROIs based on condition-related significance and then performs selective analyses (HMM state inference and condition discrimination) on those ROIs using the same dataset. Under the null (or under weaker true effects), this can create distorted statistics and inflated apparent structure because selection and evaluation are not independent. The cited work emphasizes that independence under the null is required for valid inference after selection, which is not established in the manuscript. Because the manuscript’s main conclusions rely on the strength and specificity of inferred transient states, invalid inference at this stage can undermine the conclusions. The problem affects not just p-values but also descriptive claims about which state “stands out” for a condition. Consequently, the evidence base for the reported DMN–V1 state as predictive of perceptual transitions is weakened.\n“the study demonstrates that the common practice of conducting post-hoc tests only on brain regions showing significant interaction effects can substantially increase the false positive rate in the control condition.” ([2](#ref-2))\nAlthough this quotation concerns post-hoc testing after interaction screening, the underlying mechanism is analogous: selecting regions based on significance and then performing follow-up inference on those selected regions can inflate apparent effects. The manuscript’s approach similarly narrows analysis to regions deemed “significantly engaged,” then interprets additional downstream results (HMM states and predictive accuracy). This supports the general concern that selection can bias subsequent inference unless properly controlled. In the current paper, the issue is compounded because ROI selection happens before an unsupervised model whose output is later interpreted as condition-specific. The logic that selection “increases sensitivity” can be true, but it does not eliminate false positives or circularity; it can worsen them if the same data drive both steps. Therefore, the paper’s pipeline plausibly overstates the robustness of the state–condition correspondence.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|GPT|2", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "This paper’s cross-validation evaluation is insufficiently specified and likely non-independent (Validity; Conclusions; Appropriate use of statistics), because it uses trial-level features from repeated trials within subjects with default 5-fold cross-validation and no indication of subject-wise grouping, while also using analysis windows that the authors acknowledge can mix perceptual content.\n\n“The fitting data were the Fractional Occupancies of the 4 hidden neural states in all trials. The target variable was the binary variable indicating whether the trial is transiting to a dominant or mixed percept.”\nThis describes a trial-level classifier built from many trials per participant, which creates hierarchical dependence (trials nested within subjects). If folds are created by randomly splitting trials (as is typical for default k-fold CV), then the same subject’s trials appear in both train and test sets. That setup can inflate accuracy by exploiting stable subject-specific signatures in fractional occupancy rather than learning generalizable predictors of percept type. The manuscript does not state that folds were grouped by subject or session, which is the common safeguard for repeated-measures data. Additionally, the target labels (dominant vs mixed transition) are tightly linked to the epoch definition, so the classifier may capitalize on definitional leakage rather than true prospective prediction. Without subject-wise splitting and a clear separation between model selection and evaluation, the reported accuracies are not reliable indicators of out-of-sample predictive performance.\n“We used the linear support vector machine as the estimator, and the default 5-fold CV.”\n“Default 5-fold CV” is ambiguous in the presence of repeated measures and can be inappropriate when samples are not independent. In neuroimaging/EEG datasets, multiple trials from the same person often share physiological and preprocessing artifacts that are easily learned by a classifier. Randomly splitting such trials violates the independence assumption required for unbiased error estimation. The paper does not report using group-aware splitting (e.g., leave-one-subject-out or group k-fold), nor does it describe nested CV for hyperparameter tuning beyond scanning a regularization range. This omission is significant because the claimed difference between BR and replay accuracies is used to support a mechanistic interpretation (“causal power”). If the evaluation is optimistic due to leakage, the downstream conclusion that intrinsic dynamics “predict” perceptual transitions is not well supported. Strong accuracy values (e.g., >90%) are especially suspicious under non-independent trial splitting and demand stricter validation.\n“Therefore, the 1-s window before a dominant percept may cover periods of perceptual fluctuation, including the transitional mixed percept that is meant to be captured, and the residual of dominant percept from the last trial.”\nThis admission indicates that the feature window for a labeled trial can contain perceptual content from multiple percept categories. If so, the classifier may be detecting the presence of mixed percept content already present within the 1-second window, rather than predicting an upcoming transition. In other words, the label may not be temporally well-separated from the neural activity used as input, undermining the interpretation of the model as predictive rather than descriptive. This is a major issue for the paper’s abstract-level claim that transient states predict “upcoming” involuntary transitions. Moreover, because the authors include “0.1-s post-response padding” in the targeted window, motor-related activity could further contaminate the feature set in a way correlated with report type. The combination of mixed percept contamination and potential motor contamination means the evaluation could be capturing trivial correlates of the labeling scheme. Therefore, the reported cross-validation accuracy cannot be confidently interpreted as evidence of prospective prediction of perceptual dynamics.\n“K-fold iterator variant with non-overlapping groups. Each group will appear exactly once in the test set across all folds …” ([4](#ref-4))\nThis documentation excerpt specifies the behavior of a group-aware cross-validation strategy designed for settings where samples are clustered into groups (e.g., subjects). The manuscript’s use of “default 5-fold CV” is not described as group-aware, even though the data structure is naturally grouped by participant. Group-aware splitting is a standard safeguard to prevent leakage when the goal is generalization beyond individuals. Without it, estimated accuracy can reflect memorization of group-specific baselines rather than a relationship between neural features and perceptual outcomes. The citation supports the critique that the cross-validation scheme should be aligned with the data’s grouping structure. Because the paper does not indicate the use of such methods, its predictive claims are not sufficiently supported.\n“However, when performing cross-validation, these structures are regularly ignored, resulting in serious underestimation of predictive error.” ([3](#ref-3))\nThis statement directly supports the concern that non-independent cross-validation can produce overly optimistic performance estimates. In the paper, trials are repeated measures within participants, which is a canonical example of hierarchical structure. If the cross-validation ignores that structure (e.g., random trial splits), it can substantially underestimate true error when predicting on new individuals or genuinely independent data. The paper leverages the cross-validation result to argue about “causal power” and differential predictability between BR and replay, so underestimation of error would materially affect the conclusions. The cited work also emphasizes that independence between training and evaluation data is the central assumption for valid error estimation. Because the manuscript does not demonstrate that independence, the reported accuracies are not robust evidence.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|GPT|3", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "This paper overstates the evidential strength of its Granger-causality analysis for claiming a directed “causal effect” from PCU to V1 (Validity; Conclusions), because Granger causality on EEG-derived source signals is vulnerable to confounds (e.g., volume conduction/common input) and the manuscript does not demonstrate the methodological safeguards needed to interpret the result as directed neural influence.\n\n“Granger causality is used this study to establish the causal influence from the PCu to V1 in the BR dominant condition.”\nThis sentence explicitly frames the analysis as establishing “causal influence,” which is a strong claim for Granger causality in electrophysiological data. Granger causality tests a predictive, time-lagged relationship in the observed signals, but it does not by itself establish causal influence in the interventionist sense. In EEG source space, apparent lagged predictability can arise from source leakage, common drivers, filtering artifacts, or mis-specified autoregressive models. The manuscript does not provide evidence that these confounds were mitigated (e.g., leakage correction, control for common inputs, model order validation, robustness across preprocessing choices). Moreover, the study’s key directed conclusion depends on the PCU→V1 directionality being trustworthy, so methodological ambiguity here directly affects the validity of the central mechanistic story. Without stronger controls and sensitivity analyses, the claim “establish[es]” causal influence is not warranted.\n“For model selection, we used Bayesian information criterion (BIC) … The GC effect size was approximated by the difference of the Bayesian Information Criterion (dBIC) …”\nUsing ΔBIC between a univariate autoregressive model and an augmented model is one way to quantify relative fit, but it does not automatically translate into a reliable “effect size” of directed connectivity. In short time windows (here, trials with 250 Hz sampling and short lags), autoregressive modeling can be unstable and sensitive to preprocessing, particularly if signals are not stationary. The paper does not report diagnostics such as residual whiteness, stability, or sensitivity to model order, which are important for Granger-based inference. Additionally, ΔBIC can be influenced by noise structure and shared variance due to leakage, which can create spurious improvements when adding a correlated predictor time series. The approximation of “effect size” as ΔBIC therefore requires careful justification and validation, which is not shown in the manuscript. As a result, the directed connectivity inference is methodologically under-supported.\n“To better understand the cognitive implication of the PCU-V1 coupling, which was a main feature of State 4, we further investigated the causal effect of the PCU to V1 and its relationship with behavioural measures.”\nThis sentence shows that the paper’s broader interpretation (DMN dynamics influencing perception) hinges on the “causal effect” framing of the GC analysis. Yet the paper’s own results emphasize group-level correlations and interactions, not robust trial-by-trial predictive relationships, which already weakens the causal narrative. More importantly, if GC is confounded by source leakage or common inputs, then the observed PCU→V1 relation may not reflect top-down modulation at all. The paper proposes competing interpretations (attention vs habituation) but treats GC as a causal quantity before resolving these alternatives. The lack of explicit confound control means that these interpretations could be built on an unreliable directed measure. Therefore, the “causal effect” conclusion is not robust given the methodological information provided.\n“Next, we highlight a number of interpretational caveats and common pitfalls that can arise when performing functional connectivity analysis, including the common reference problem, the signal to noise ratio problem, the volume conduction problem, the common input problem, and the sample size bias problem.” ([5](#ref-5))\nThis statement enumerates several pitfalls that are directly relevant to Granger-causality inference in EEG/MEG. In particular, volume conduction and common input can generate spurious apparent connectivity (including directional measures) if not explicitly addressed. The manuscript does not report how it handled these pitfalls for source-level GC, nor does it provide validation analyses demonstrating robustness to such confounds. Because the cited tutorial frames these issues as common and important, omitting safeguards in the paper’s methods is consequential rather than cosmetic. The reliance on GC to support a directed PCU→V1 influence therefore falls short of common methodological expectations in electrophysiological connectivity studies. This weakens the validity of the paper’s mechanistic claims about DMN-to-visual cortex modulation.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|GPT|4", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "This paper’s EEG source reconstruction appears to incorporate condition-dependent fMRI-derived priors, risking circular inference (Validity; Data and methodology), because it uses group-level fMRI activation clusters from the same experiment to constrain EEG source inversion in a condition-specific manner and then interprets source differences as evidence for DMN involvement and uses them to guide later ROI/HMM analyses.\n\n“According to the condition type, i.e. stimuli types (BR vs. RPL) × perceptual types (dominant vs. mixed) that the reported perceptual change belongs to, the corresponding group-level fMRI (significant) activation clusters were applied to constrain the sources’ covariance for the model inversion.”\nThis sentence indicates that the inverse solution is constrained using priors that depend on the condition label of the epoch being reconstructed. That creates a risk that condition differences in fMRI activation are effectively injected as priors into the EEG source estimates, making subsequent EEG source contrasts less independent. If different priors are applied for different conditions, the reconstructed sources may differ partly because the inversion was encouraged to differ, not purely because the EEG data differ. This is especially problematic when the reconstructed sources are later interpreted as evidence about where the EEG effect “comes from,” because the inversion procedure itself uses condition information. Standard practice for fMRI-informed EEG inversion typically requires careful separation of data used for priors from data used for inference (e.g., orthogonal contrasts, independent datasets, or priors held fixed across conditions). The manuscript does not demonstrate such separation here. Therefore, the validity of source-localized DMN/V1 conclusions is undermined.\n“To discover the brain location of the signals that generated this scalp topological difference, we then conducted source reconstruction for the ERPs during this time window. The source reconstruction indicated that the topology was driven by a deactivation in the posterior cingulate cortex (PCC; BA23/24), precuneus (PCU; BA31/7m), thalamus, insula, caudate, claustrum and the fusiform gyrus (BA20) during BR (dominant) vs. RPL (dominant) condition …”\nThe main paper treats the source reconstruction output as evidence for the anatomical generators of the ERP differences and highlights DMN-related regions (PCC/PCU). If the reconstruction is influenced by condition-specific fMRI priors, then the anatomical “indication” is not purely data-driven from EEG. That matters because these regions become central to the paper’s mechanistic narrative about intrinsic DMN dynamics. The manuscript also uses these source-level results to motivate later ROI restriction for HMM analyses, so any bias in source localization can propagate to later steps. Without clear reporting that priors are independent or held constant across contrasted conditions, the localization claim is not robust. This creates a validity issue for conclusions about DMN nodes being the drivers of the pre-transition EEG patterns.\n“To increase the sensitivity of the method as well as to avoid overfitting, we constrained our regions of interest to those which were shown to be significantly engaged in the experiment by the source-level evoked EEG activation contrasts between experimental conditions.”\nThis sentence shows that the downstream HMM ROI selection explicitly depends on the source-level contrasts. Therefore, any circularity or bias in source reconstruction does not remain confined to one figure; it can shape the entire analysis pipeline. If the source reconstruction is guided by fMRI priors that differ by condition, then the “significant” source-level contrasts used for ROI selection could be partially driven by the prior structure. That would make the HMM results less reliable because the input ROI signals were chosen based on potentially biased source estimates. This also undermines the paper’s claim that ROI restriction was primarily to avoid overfitting, since it may instead amplify condition-separable structure. The paper does not provide an ablation showing that conclusions hold without fMRI priors or with priors fixed across conditions. As a result, the validity of the entire EEG source-to-HMM chain is weakened.\n“However, selection among noisy measurements can render circular an otherwise appropriate analysis and invalidate results.” ([1](#ref-1))\nThis sentence captures the core concern: when analysis decisions are conditioned on noisy results (here, “significant” activation clusters and condition-specific priors), subsequent inferences can become circular. In the manuscript, fMRI-derived significant clusters appear to be used to constrain EEG inversion, and EEG source contrasts then inform ROI selection and state modeling. This multi-stage selection and constraint can create a pipeline where each stage reinforces the same condition differences, even if some differences are driven by noise or modeling choices. The cited warning is therefore directly applicable, because the paper’s approach uses selection/constraints based on the same experimental conditions whose neural signatures are later interpreted. Without an explicit strategy to maintain independence across stages, statistical inference and anatomical interpretation can be invalidated. This is a major validity threat because it targets the methodological foundation of the reported DMN–V1 dynamics.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|GPT|5", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "This paper’s results are not practically reproducible from the provided code and materials (Data and methodology; Validity), because the included “code” package does not contain executable analysis scripts or a complete pipeline, while the methods rely on multiple external toolboxes (including proprietary MATLAB) and external intermediate-result repositories.\n\n“All data needed to evaluate the conclusions in the paper are publicly available in the repository: (https://datadryad.org/stash/dataset/doi:10.5061/dryad.bflb1).”\nThis statement suggests that availability of the dataset is sufficient to evaluate the conclusions, but the manuscript’s analyses are computationally complex (EEG–fMRI source reconstruction, embedded-lag HMM, Granger causality, permutation testing). Data access alone rarely enables reproduction without the exact code, parameter settings, and preprocessing scripts used to derive the reported figures and statistics. In particular, the paper’s key outcomes depend on multi-stage modeling decisions (ROI extraction, HMM settings, CV, GC model order) that are not fully reconstructable from the paper text alone. The provided code bundle in this review package does not include scripts to run these steps end-to-end. Therefore, an independent researcher cannot straightforwardly “evaluate the conclusions” by rerunning the analysis using only the shared materials. This weakens the paper on reproducibility and transparency.\n“To replicate the results of the project, apart from carrying out the pipeline right from the beginning with the original data; the reader/reviewer can also partially test some of the results in the midway.”\nThe README acknowledges that replication requires carrying out a full pipeline, which implies the existence of a detailed set of scripts and intermediate artifacts. However, the code package provided here contains only this README and a license, and does not include the pipeline scripts needed for replication. The README’s suggestion to “partially test” results depends on access to stored “intermediate results” located in an external GitHub repository, which is not archived or version-pinned in the package being reviewed. This makes the analysis dependent on external resources that can change over time and are not guaranteed to be available or identical to what the authors used. It also prevents verification of how intermediate results were created, which is essential for scientific reproducibility. As a consequence, the reproducibility of the study’s computational claims is materially limited.\n“## Essential toolboxes:\n\n1.  MNE: https://mne.tools/dev/install/index.html\n2.  HMM-MAR-master: https://github.com/OHBA-analysis/HMM-MAR/\n3.  granger_cause_1: https://uk.mathworks.com/matlabcentral/fileexchange/59390-granger_cause_1\n4.  spm12: https://www.fil.ion.ucl.ac.uk/spm/software/spm12/\n\n## Required dependencies and compatible software versions:\n1.  Matlab2016a\n2.  Python3\n3.  Nilearn>=0.5.1”\nThis excerpt documents substantial external dependencies, including proprietary MATLAB (2016a) and specialized toolboxes (SPM12, HMM-MAR, third-party Granger code). Such dependencies can be acceptable, but reproducibility requires the analysis scripts, parameter files, and versioning to be provided so others can re-run the exact workflow. Merely listing toolboxes does not make the analysis executable, because the precise calls and settings (e.g., HMM parameters, source reconstruction configuration, cross-validation settings, and preprocessing details) are not encoded. Additionally, toolboxes evolve; without pinned versions or an executable environment specification, rerunning the pipeline can yield different outputs. The reliance on multiple toolchains (MATLAB + Python) further increases the need for automated scripts and run instructions. Since these are not included in the provided code bundle, the study is not reproducible from the supplied materials.\n“There is an urgent need to improve the infrastructure supporting the reuse of scholarly data.” ([6](#ref-6))\nThis statement emphasizes that reuse requires infrastructure beyond merely hosting data files. In computational neuroscience, such infrastructure typically includes the full analysis code, provenance of intermediate derivatives, and machine-executable workflows. The paper asserts that the data are publicly available, but the present packaging does not provide the necessary computational artifacts to reuse the data to reproduce the conclusions. Moreover, the FAIR principles stress that design choices should enable reuse by others, which is not met when key steps are only described narratively and implemented in unavailable scripts. Because the core contributions of the paper are quantitative and model-based, the absence of an executable pipeline is a significant methodological limitation. This is not a minor documentation gap; it directly prevents independent verification. Consequently, the paper falls short of common reproducibility expectations for data-driven neuroimaging studies.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "The paper claims to \"predict\" involuntary fluctuations of visual awareness, but the results only demonstrate a group-level correlation between brain state properties and the rate of perceptual alternation, failing to predict trial-by-trial switches.\n\n\"Perturbation or Function? Intrinsic brain dynamics in the Default Mode Network predict involuntary fluctuations of visual awareness\"\nThe title explicitly claims that intrinsic dynamics \"predict\" the fluctuations, implying a temporal prediction of specific perceptual switches.\n\"That neither state properties nor Granger-causality from PCU to V1 could predict trial-by-trial performance may just be due to a lack of statistical power; however, it could also be a true negative.\"\nThe authors explicitly admit that their model failed to predict the perceptual switches on a trial-by-trial basis. This directly contradicts the strong claim made in the title and abstract. A correlation with the *rate* of fluctuation across subjects (individual differences) is fundamentally different from predicting the *occurrence* of a fluctuation in time.\n\"However, this relationship only existed on the group level, but not for trial-by-trial prediction; therefore, it only establishes the behavioural relevance of the causal effect of PCU to V1\"\nThis further confirms that the finding is limited to between-subject variability, not the dynamic prediction of the perceptual process itself.\n\"we found that the intrinsic transient states exhibited in the posterior subdivisions of the DMN were characterised by high power and total coherence in the alpha (8-12 Hz) range\"\nWhile this describes the state, it does not support the claim of prediction if the state's occurrence does not reliably precede the switch on a single-trial level.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "The analysis window of -400 to -200 ms relative to the subjective report likely overlaps with the post-perceptual reaction time period, meaning the observed neural activity may reflect motor preparation or the consequence of the switch rather than its cause.\n\n\"Permutation cluster tests on the Global Field Power (GFP) of the perceptual conditions revealed that the most eventful epoch was between [-400-200] ms, which was when the EEG sensor voltages differed the most between the endogenously (BR) and exogenously (RPL) generated dominant percept\"\nThe authors identify the critical window as 400 to 200 ms before the button press. However, the reaction time to report a perceptual switch in binocular rivalry is typically in the range of 400-600 ms [1].\n\"We used the moment of subjective reports as the critical timepoint and created the event-related BOLD response\"\nBy aligning to the report, the analysis ignores the variable delay between the internal perceptual switch and the motor action. If the reaction time is around 500 ms, the -400 ms timepoint corresponds to 100 ms *after* the perceptual switch has likely occurred.\n\"Binocular Rivalry: Frontal Activity Relates to Introspection and Action But Not to Perception\" [2]\nThis paper (cited as [57] in the manuscript) argues that frontal and parietal activity often attributed to the switch is actually related to the report (introspection and action). The current study's finding in the -400 to -200 ms window is highly susceptible to this confound.\n\nReferences:\n[1] <https://www.jneurosci.org/content/31/28/10293>\n[2] <https://www.jneurosci.org/content/34/5/1738>", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "The manuscript lacks a detailed description of the Hidden Markov Model (HMM) and Granger Causality analyses, including model specification, state selection criteria, and validation steps, which prevents reproducibility.\n\n\"The 4 brain states, found in a data-driven way, turned out to be phenomenologically meaningful\"\nThe text mentions finding 4 states but does not explain how the number of states was determined (e.g., free energy, cross-validation) or what features were input into the HMM (e.g., raw signal, envelope, frequency bands).\n\"To further understand this signal coupling, we have also derived a Granger-causal effect of the PCU to V1 from their EEG signals at the same time windows.\"\nThere is no section in the main text or the provided supplementary materials that describes the Granger Causality method used (e.g., time-domain vs. frequency-domain, model order selection, stationarity checks).\n\"Our subsequent dynamic analysis will mostly focus on these regions.\"\nThe transition from the fMRI/EEG activation results to the dynamic analysis (HMM/Granger) is abrupt, with no methodological details provided in between.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "The authors propose that DMN \"perturbation\" or \"ignition\" drives the perceptual switch, but their data shows DMN deactivation (or high alpha inhibition) relative to the control condition, which contradicts the notion of an active perturbation.\n\n\"Recent theoretical developments in brain dynamics suggest that the spontaneous information propagation may be empowered by the intrinsic ignition of neural activity\"\nThe authors frame their hypothesis around \"ignition\" and \"perturbation\", which implies an increase in activity or excitability.\n\"The source reconstruction indicated that the topology was driven by a deactivation in the posterior cingulate cortex (PCC; BA23/24), precuneus (PCU; BA31/7m)... during BR (dominant) vs. RPL (dominant) condition\"\nThe empirical finding is a *deactivation* (lower activity) in the DMN nodes during the critical window compared to the Replay condition.\n\"Vidaurre et al. (2018) found that the intrinsic transient states exhibited in the posterior subdivisions of the DMN were characterised by high power and total coherence in the alpha (8-12 Hz) range\"\nHigh alpha power is typically associated with functional inhibition [3]. If the \"critical state\" (State 4) is characterized by high alpha (as implied by the PCU-V1 coupling), it represents an inhibited state, not an \"ignition\". The authors fail to reconcile this \"inhibition/deactivation\" with their \"perturbation/ignition\" framework.\n\nReferences:\n[3] <https://www.frontiersin.org/articles/10.3389/fnhum.2010.00186/full>", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Gemini|5", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "The comparison between Binocular Rivalry (BR) and Replay (RPL) is confounded by the strong exogenous sensory transients present in Replay but absent in BR, making it difficult to attribute differences solely to \"intrinsic\" dynamics.\n\n\"The global field power (GFP) in the replay condition was significantly higher than that in BR condition from 400-200 ms before the report\"\nThe significantly higher GFP in Replay suggests that the physical change in the stimulus drives a strong evoked response. The \"deactivation\" observed in BR relative to Replay might simply reflect the absence of this strong sensory-driven potential, rather than a specific \"dip\" or intrinsic dynamic unique to BR.\n\"In a perceptually matched Replay (RPL) condition... the same rotating images... alternated in time\"\nAlthough perceptually matched, the Replay condition involves a physical change in the stimulus that triggers bottom-up processing mechanisms (and likely attention shifts) that are fundamentally different from the spontaneous reorganization in BR. Attributing the difference to DMN \"perturbation\" ignores this fundamental stimulus difference.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "The results of the power analysis that led to 20 participants were not included or described (even if previously published) (Is there sufficient power for this study?)", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Presumably, gaze was tracked throughout the entirety of the experiment, but this was not mentioned or described", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Several contrasts were conducted, though thresholds and multiple comparison details should be further emphasized in the corresponding sections", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "The analyses that were conducted at the individual vs group level should be more clearly indicated / separated in the text", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "A brief Methods section included in the main text would be useful in guiding the reader, in addition to have a full-length version of the Methods in the supplementary section", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_1|9", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Given the involvement of the DMN and the link found between PCU and V1, it would be good to explore how the other DMN regions affect (if at all) the PCU > V1 relationship for perceptual transitions (e.g., through dynamic causal modeling?)", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_1|11", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Although the DMN is the large-scale network of focus here, a short mention of whether it is the only source of perturbations to result in perceptual fluctuations and/or how the other large-scale networks mentioned might be involved in producing visual awareness", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_1|12", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Abstract: “causal effect” could be further clarified in terms of Granger causality", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_1|13", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "FMRI activation study (this subheading might suggest that an entirely separate study was conducted): “over- lapped” should be changed to ‘overlapped’", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_1|14", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Fig. 2/legend: Acronyms should be defined in full when first mentioned (e.g., ICN, BM, FCPN)", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_1|15", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Hidden neural states within DMN … subsection: the HMM acronym should be defined (this acronym is only defined in the supplementary section)", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_1|16", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Fig. 5 legend: “pair-wise” should be ‘pairwise’, “(clock-wise)” should be ‘(clockwise)’", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_1|17", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Fig. 5 legend: font size of cortical region names on the circular bundle plots is quite small", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_1|18", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "PCU-V1 phase … subsection: “Therefore, we next focused into..” – the ‘into’ should be changed to ‘on’ or similar", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_1|19", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "There are two “PCU-V1 phase coherence and Granger Causality predicts stable percepts” subheadings", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_1|20", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "The acronym for Granger Causality should be provided (GC)", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_1|21", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Mentions of results found in supplementary section should be expanded into statements about what those results show, in addition to where in the supplementary section they can be found", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_1|22", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "(“All statistical models have been presented..”) – the first letter of the first word in these brackets should be lowercase", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_1|23", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Discussion, paragraph 1: “namely, the interaction of them” should be “namely, this interaction”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_1|24", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "There is considerable focus in the discussion on the role of SPL, despite the results focusing on PCU/V1", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_1|25", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "“on the group level” should be “at the group level”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_1|27", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Supplementary: “>3mm displacement” might be amended to “translations and/or rotations of > 3mm/°, respectively”, given that both factors (indicated in mm or °) are accounted for in motion correction", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_1|28", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Supplementary: “on Python” could be “(implemented) in Python”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_1|29", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Supplementary: here it is “PCu”, whereas it is “PCU” in the main text", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_1|30", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Supplementary, sFig. 3: no regions are labeled on the brains, nor are they mentioned in the legend (and scale label font size is quite small – same for sFigs. 4, 10, 11, 12, 13, 14)", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_1|31", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Supplementary, Table 2: in the main text, this table is actually referred to as Table 1 when the coordinates are discussed; there is no mention of why there are different numbers of coordinates for each of the regions", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Complexity\\n\\nFirst of all the extensive set of data analysis tools makes the manuscript highly demanding and comes with a considerable danger to loose a large number of readers, simply due to complexity reasons. I regard it thus as urgently necessary to fulfill some minimal requirements to make the manuscript easier to understand.\\n\\n1.1. Resolving Shortcuts\\nOne urgent suggestion is, of course, that EVERY shortcut used should at least once be spelled out. In the present manuscript there are many examples, where this is not the case, e.g. “ICN”, “BM” or ECG (in the supplementary material).\\n\\n1.2. Provide intuitive explanations\\nThe authors should also provide for any statistical tool 1 – 3 sentences that explain the basic idea. I was personally unfamiliar with many tools and had to stop reading several times, in order to look for myself for the underlying literature and receive a basic idea, what certain methods, where only their names were mentioned, do. A reader should be able to go through the manuscript with at least a basic understanding of the logic underlying a certain analysis step, without extensively studying secondary literature. To be honest, the help of the extensive supplementary material, provided by the authors, was also very limited in this respect.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "“causal effects”\\n\\nAll of us know that our current knowledge about brain processing does not really allow making strong statements about causation. This was even emphasized by Dr. Granger, when he presented his Granger Causality. The authors should thus be careful with making strong statements about causality (e.g. page 23) …", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "The endogenously/ exogenously dominant percepts are used interchangeably with BR/RPL. For ease of reading it might be good to stick to either using endogenous/exogenous or BR/RPL after defining which condition is which", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Time course of perceptual reversals\\n\\nUnderstanding the neural processes underlying spontaneous perceptual reversals, the precise time point of the reversal event is necessary, e.g. in order to know which activity is pre-reversal and which activity is post-reversal and probably even secondary to the reversal-related neural processes. Narrowing down the reversal time point, however, is difficult – in the first place, because the reversal is an endogenous brain process and the experimenter only gets to know about it, when the participant communicates her/his first person experience of the endogenous event. Using iris diameters or eye-movement patterns in non-response paradigms (Brascamp et al. 2018) is an interesting perspective but apparently provide not precise enough time stamps.\\nSeveral years ago we have designed the so-called onset-paradigm (a simpler version primarily introduced by O’Donnell et al. 1988) to study the chain of processes underlying a spontaneous perceptual reversal of the Necker cube and other ambiguous figures (for a review see Kornmeier and Bach 2012). In a nutshell, the basic idea was to present the stimuli discontinuously (800 ms on, 400 ms off), and therewith to synchronize the onsets of perceptual reversals with the onset of the stimulus and thus use stimulus onset as time reference for the reversal event. This allowed us a remarkable temporal resolution of the processes underlying Necker cube reversals, which we then compared with a related chain of processes when disambiguated cube variants reversed in a computer-driven manner. We found remarkable similarities but also interesting differences. Both our group and Michael Pitts and colleagues demonstrated that the basic idea of the onset paradigm also works with binocular rivalry stimuli and moreover, that similar results can be measured (for a review see Pitts and Britz 2011), although we were not as successful to show this for BR stimuli (O’Shea et al. 2013).\\nRelevant for the present manuscript are the following findings:\\nOur group (Ehm et al. 2011) and concurrently and independently Britz et al. (Britz et al. 2009) found right-hemispheric EEG activity in the gap immediately before (around 100-300 ms) an endogenous perceptual reversal. The onset-paradigm thus clearly allowed confining this right-hemispheric activity to a pre-reversal time window. This may be a relevant finding for the authors’ discussion in the second paragraph of their page 22.\\nFurther, we found that reaction times jitter intra-individually with ± 100 ms (interquartile range) and discussed this in relation to the reversal event (Kornmeier and Bach 2012). The authors of the present manuscript use participants’ manual response as reference time point. They thus need to take into account that the reversal event had occurred about 100 ms earlier. The zero point in their graph is thus not the time point of the reversal but rather the time point ± 100 ms after the reversal. Given our data, the authors may even consider shortening their temporal ROI (in a follow-up analysis or follow-up experiments), which may increase the signal-to-noise ratio of the reversal-related signals.\\n\\nOf course it is always a little problematic if a reviewer requires the authors to cite his own work. However, in the current case this may be defensible: The authors made a big effort to narrow down the processes underlying spontaneous perceptual reversals both in time (focusing on causal aspects) and in space. In our view our onset paradigm provides the most precise temporal description of the processing chain underlying spontaneous perceptual reversals. And although there are significant differences between classical ambiguous figures, like the Necker cube, and binocular rivalry stimuli, there seem to be also several similarities, particularly concerning processing chains, as Pitts and Britz (Pitts and Britz 2011) worked out in their review, but as also much earlier Blake and Logothetis pointed out in their seminal review (Blake and Logothetis 2002). Furthermore our findings have since been replicated by several labs around the globe (e.g. Pitts et al. 2007; Intaite et al. 2010; Sandberg et al. 2014; Kornmeier et al. 2019; Abdallah and Brooks 2020). We thus think that this work needs to be at least discussed in relation to the authors’ findings.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Page 2: “…We know that external perturbations can interrupt or bias the global cascades of information propagation (e.g. visual masking and priming) …“\\n\\nIn the sentences before the cited one, the authors elaborate about resting state brain activity. I think in the cited sentence they write instead about processing of sensory information. However, this is not entirely clear. By this reason it is also not really clear how visual masking and priming fit into this sentence. The authors should explain the ideas behind this sentence in more detail and add some references from the priming and masking literature.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Page 2: In 2001 Randolph Blake provided an encompassing review about BR. The authors should consider citing this profound work (Blake 2001), when they introduce the BR stimuli.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Page 3, end of paragraph 1: Sentence is difficult to read “…However, the intrinsic dynamics of brain networks may have a lot of interactions with, and by which modulate, the activity of local sensory regions.”\\n\\nBetter: “However, the intrinsic dynamics of brain networks may have a lot of interactions with the activity of the local sensory regions, and as a result modulate said region.”\\n- define “RSS”\\n- “Akaike Information Criterion“ => provide at least one informational sentence about what this measure does …", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_2|10", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Page 6: The present manuscript only indicates in a sub clause, that parts of the data have already been analyzed and the results published in another paper. The authors should make this more explicit. Moreover, they need to indicate what the major difference and “unique selling point” of the present data analysis in comparison to the previous publication is.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_2|11", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Page 6, Fig. 1: It is reasonable to represent data from red and green stimuli in the same colors (Fig. 1). However, it may be hard to distinguish for some of your readers (9% of men, 0.8 % of women). Consider using shadings in addition to color coding. Further, it is unclear to me why in Fig. 1d there are symbols (triangle and diamond) behind the boxplots. Does this address the color-blindness problem? To me it looks confusing and a simple shading would already do the trick with only little visual clutter.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_2|12", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Page 8, Fig. 2: Define FPCN and ICN", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_2|13", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Page 8, line 2 of section “EEG evoked responses and source reconstruction”: “The EEG recording with its excellent temporal resolution gave us the opportunity to better locate the neural cause of a perceptual change…” How do we know if it s a cause? Could it not simply be a correlation?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_2|14", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Page 8, Fig. 2: BM14 is listed on the circular plot but not in the text next to it.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_2|15", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Page 10: What is the exact logic behind the selection of the time window for voltage map subtractions in Fig. 3d right.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_2|16", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Page 11, line 22: “…We targeted our dynamic analyses at the temporal window of the second (with 0.1-s post-response padding) before every perceptual transition as a trade-off between having enough sample points and having enough specificity for the targeted events.”\\nThis should read: “… before every response of a perceptual transition…”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_2|17", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Page 12: The arguments for the a priori choice of 4 states is not entirely clear to me.\\nThe authors wrote: “…We chose 4 states because firstly we were interested in the differences of the neural activity among the four experimental conditions…”\\nDoes this argument make sense if one can assume that each of the four (or more) microstates can occur within each of the four conditions? Exactly this is what I observe in Fig. 4 bottom right. This point needs more clarification!", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_2|18", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Page 13, Legend to Figure 4: “… Across all the experimental conditions, signals from significant peak voxels within the same ROIs were averaged … “\\nFor me this sentence is not clear. Essentially the authors have spatial and temporal ROIs. I suppose they average across the data within a temporal ROI but I am not sure. This should be explained in more detail.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_2|19", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Page 14: The authors should clarify that a mixed perceptual transition means a transition from a stable percept to a mixed percept (if I am right) … and the respective for dominant perceptual transitions …", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_2|20", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Page 18: “… In the BR literature, it is commonly believed that a switch of perception is\\n\\ncaused by a slip of equilibrium due to neuronal noise, and/or the constant decay of suppression that one neural population has over the other, due to habituation effects (10, 11, 44). Apart from these, attention effects have also been shown to play a role (10, 45).\\n\\nTherefore, the PCU→V1 top-down modulation could reflect either an intrinsically evoked attention effect, or an effect of the global adaptation/perceptual habituation. These two possibilities would lead to opposite trial-by-trial predictions. …“\\n\\nI cannot completely follow these considerations. There is indeed a debate about whether perceptual reversals are driven in a bottom-up manner or rather in a top-down manner. I am fine up to this point. However, attention-induced higher reversal rates are only reported if participants are explicitly instructed to volitionally increase reversal rates. The latter is more effective for classical ambiguous figures than for BR stimuli. However, without instruction, I do not see the case that higher reversal rates should be expected.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_2|21", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Page 20, Figure 6: Please define “dBIC”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_2|22", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Page 4: “… Therefore, this paradigm had a 2×2 factorial design of dominant and mixed perception types for the BR and RPL conditions … “\\nYou may change this sentence to:\\n“… Therefore, this paradigm had a 2×2 factorial design of dominant (red and green percepts taken together) and mixed perception types for the BR and RPL conditions … “", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_2|23", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Page 5 first paragraph: “… formeda…” => “… formed a …”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_2|24", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Page 5 line 11: “greenpercept” -> “green percept”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_2|25", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Page 6, Figure 1 line 7: “…can generate alternating percept…” -> “… can generate alternating percepts”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_2|26", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Page 7: “… over- lapped … “ => “… overlapped … “", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_2|27", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Page 11, line 11: Should the reference not be of the paper instead of the URL? -> Diego Vidaurre, Andrew J. Quinn, Adam P. Baker, David Dupret, Alvaro Tejero-Cantero and Mark W. Woolrich (2016) Spectrally resolved fast transient brain states in electrophysiological data. NeuroImage. Volume 126, Pages 81–95. => At least the reference should also be added!", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_2|28", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Page 18, line 7: Same section title as above", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_2|29", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Page 18, line 12: “onthe” -> “on the”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_2|30", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Page 22: fMRIactivation => fMRI activation", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_2|31", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "There are some formatting problems with reference number 36.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "They first found reduced global field power (GFP) in BR vs. RPL condition at about 300ms before the button report of dominant percept. Source localization based on the prior of fMRI activation revealed deactivation of a range of brain areas including some of the DMN nodes. However, the fMRI results didn’t reveal any deactivations. Then they used a four states Hidden Markov Modeling (HMM) algorithm to fit the time course of EEG sources from DMN regions and V1. The occupancy of state 4 was found much longer for the rivalry than the replay condition. Although there were also obvious differences in other states, they used state 4 for the following analysis. Then a spectrum analysis was performed on power and coherence of different frequency bands between different regions from different states. Only alpha band result was used the following analysis. For the alpha coherence, state 4 shows significant PCU-V1 phase coherence. The PCU-rIPL coherence was also significant, but it was not mentioned in the text. Then they selected the PCU-V1 coherence for granger causality analysis and found no correlation of GC->V1 with perceptual duration at the trial-by-trial level. But there was a correlation at the group level only when the trial was dominated by state 4. Then they came to the conclusion that the causal effect from precuneus (PCU) to V1 can predict the following duration of perceptual state.\\n\\nThese are some interesting results from these analyses, but the main conclusion comes from a long way with many steps of arbitrary selections. Thus I feel the evidence for the final conclusion are relatively weak.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|16|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb16", "comment": "Another major concern is for the definition of time of perceptual switch. The current study used the button press of perceptual report for the time of switch, while the human reaction time on average is about 400ms. The deactivation they found on the EEG signal (about 300ms before button press) may occur after the perceptual switch. Thus the DMN activity they found associated with this time period should be a consequence rather than the cause of conscious perception. I suggest the author to use the frequency tagging from the EEG signals to decode the “real” perceptual switch from the visual cortex.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|17|Claude|1", "source": "prb", "split": "test", "paper_id": "prb17", "comment": "The paper excludes MMS1 data from the observation-simulation comparison specifically because it does not show the bifurcated current structure, introducing potential confirmation bias in validating the simulation results against spacecraft observations.\n\n\"Data from MMS2, MMS3, and MMS4 from 20:24:00 to 20:24:15 UT on June 17, 2017 were averaged to yield the profiles shown in Figs. 5a-e. MMS1 data were omitted because the current density did not exhibit an obvious bifurcated structure.\"\nThis statement reveals that one of the four MMS spacecraft was excluded solely because its data did not conform to the expected bifurcated structure. In multi-spacecraft missions like MMS, all four spacecraft are designed to provide simultaneous measurements at different spatial locations within the same phenomenon. Excluding data from one spacecraft because it does not show the expected signature is methodologically problematic and could constitute confirmation bias. The spatial separation between spacecraft (~50 km during this period, as indicated in the MMS mission design [[1]](#citation-list)) may provide physically meaningful information about the structure's non-uniformity rather than being a reason for data exclusion. Standard multi-spacecraft analysis methods, such as the curlometer technique or multi-point timing analysis, typically require all four spacecraft measurements to properly characterize current sheet structures [[2]](#citation-list).\n\"Apart from such reconnection-related dissimilarities, the observed and simulated profiles agree strikingly well, including the bifurcated current structure.\"\nThe claim of \"striking agreement\" is made after excluding the spacecraft that showed contradictory evidence. If MMS1 did not show bifurcation while MMS2, 3, and 4 did, this spatial variability could indicate that the current sheet is more complex than the 1D equilibrium model predicts, or that the observed bifurcation is spatially localized rather than a universal feature. The paper does not provide any scientific justification for why MMS1 data should be excluded other than disagreement with the expected result.\n\nReferences:\n[1] [Burch, J. L., Moore, T. E., Torbert, R. B. & Giles, B. L. Magnetospheric Multiscale Overview and Science Objectives. Space Sci. Rev. 199, 5–21 (2016)](https://link.springer.com/article/10.1007/s11214-015-0164-9)\n[2] [Dunlop, M. W., Balogh, A., Glassmeier, K.-H. & Robert, P. Four-point Cluster application of magnetic field analysis tools: The Curlometer. J. Geophys. Res. 107, 1384 (2002)](https://agupubs.onlinelibrary.wiley.com/doi/10.1029/2001JA005088)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|17|Claude|2", "source": "prb", "split": "test", "paper_id": "prb17", "comment": "The particle-in-cell simulation uses a frequency ratio ωce/ωpe = 5, which is significantly higher than typical magnetotail conditions (where ωce/ωpe < 1), potentially affecting the electron dynamics critical to the bifurcation mechanism.\n\n\"The simulation run with a frequency ratio of ωce/ωpe = 5 is shown in this paper for clarity of presentation; ratios as low as ωce/ωpe = 0.2 were also tried, but lower ratios simply increased the duration of plasma oscillations that either damp or travel away from the center without any noticeable effect on the core relaxation mechanism.\"\nThe frequency ratio ωce/ωpe determines the relative importance of electron cyclotron motion versus plasma oscillations. In the Earth's magnetotail, typical values are ωce/ωpe ~ 0.1-0.5 [[3]](#citation-list), making the authors' choice of ωce/ωpe = 5 about 10-50 times larger than realistic values. While reduced parameters are common in PIC simulations for computational efficiency, such extreme departures from physical values require careful justification. The electron plasma frequency to cyclotron frequency ratio is a crucial parameter for accurately evaluating electron dynamics in current sheets [[4]](#citation-list). The dismissal of lower ratios as merely \"increasing duration of plasma oscillations\" does not adequately address whether the core physics is preserved under such extreme parameter choices.\n\"10,000 particles were placed per cell per species, so about 6 × 10^8 particles were simulated with a mass ratio mi/me = 100.\"\nThe reduced mass ratio mi/me = 100 (compared to the realistic value of ~1836) is a common practice in PIC simulations and is acknowledged as necessary for computational feasibility. However, combined with the extreme frequency ratio, the simulation operates in a parameter regime that is doubly removed from realistic magnetospheric conditions. While mass ratio reductions are generally well-understood [[5]](#citation-list), the combined effect of both reduced mass ratio and extreme frequency ratio on the orbit class transitions and equilibration dynamics has not been demonstrated to be negligible.\n\nReferences:\n[3] [Artemyev, A. V., Petrukovich, A. A., Nakamura, R. & Zelenyi, L. M. Cluster statistics of thin current sheets in the Earth magnetotail: Specifics of the dawn flank, proton temperature profiles and electrostatic effects. J. Geophys. Res. 116, A09233 (2011)](https://agupubs.onlinelibrary.wiley.com/doi/10.1029/2011JA016801)\n[4] [Artemyev, A. V. et al. The electron plasma frequency to cyclotron frequency ratio as a crucial parameter for electron dynamics in current sheets. Physics of Plasmas 27, 072904 (2020)](https://pubs.aip.org/aip/pop/article/27/7/072904/1061692)\n[5] [Birn, J. et al. Geospace Environmental Modeling (GEM) Magnetic Reconnection Challenge. J. Geophys. Res. 106, 3715–3719 (2001)](https://agupubs.onlinelibrary.wiley.com/doi/10.1029/1999JA900449)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|17|Claude|3", "source": "prb", "split": "test", "paper_id": "prb17", "comment": "The paper compares a 1D non-reconnecting PIC simulation equilibrium to an MMS-observed current sheet that is actively undergoing magnetic reconnection, making the comparison fundamentally inconsistent despite qualitative similarities.\n\n\"The finite electron outflow veL in Fig. 5b indicates that the observed current sheet is undergoing magnetic reconnection, whereas the simulated current sheet, being one-dimensional, is not.\"\nThe authors acknowledge that the observed and simulated systems are in qualitatively different physical states. Magnetic reconnection fundamentally alters the current sheet structure, particle distributions, and energy balance. Reconnection drives electron heating at the sheet center [[6]](#citation-list), creates characteristic velocity signatures, and can produce bifurcated structures through mechanisms entirely different from the orbit class transitions proposed in this paper [[7]](#citation-list). Comparing a 1D equilibrium to an actively reconnecting current sheet and attributing the differences simply to \"reconnection-related dissimilarities\" underestimates the fundamental incompatibility of the two systems.\n\"Reconnection induces perpendicular electron heating at the sheet center, which explains the central increase of TeMM in Fig. 5d relative to Fig. 5j. The relative increase of TeLL at the outskirts in Fig. 5d is also attributed to reconnection-induced parallel electron heating.\"\nThe authors attribute multiple discrepancies between observation and simulation to reconnection effects, which raises the question of what fraction of the observed structure is due to the proposed orbit class equilibration versus ongoing reconnection dynamics. Bifurcated current sheets have been previously explained as consequences of magnetic reconnection itself [[7]](#citation-list), [[8]](#citation-list). The paper does not provide a quantitative assessment of how to separate reconnection-induced features from equilibration-induced features in the MMS observations.\n\nReferences:\n[6] [Shay, M. A. et al. Electron heating during magnetic reconnection: A simulation scaling study. Phys. Plasmas 21, 122902 (2014)](https://pubs.aip.org/aip/pop/article/21/12/122902/282626)\n[7] [Gosling, J. T. & Szabo, A. Bifurcated current sheets produced by magnetic reconnection in the solar wind. J. Geophys. Res. 113, A10103 (2008)](https://agupubs.onlinelibrary.wiley.com/doi/10.1029/2008JA013473)\n[8] [Hoshino, M. et al. Structure of plasma sheet in magnetotail: Double-peaked electric current sheet. J. Geophys. Res. 101, 24775–24786 (1996)](https://agupubs.onlinelibrary.wiley.com/doi/10.1029/96JA02313)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|17|Claude|4", "source": "prb", "split": "test", "paper_id": "prb17", "comment": "The paper examines only a single type of disequilibrium (under-heated Harris sheet with T = 0.2Teq) without demonstrating that the orbit class transition mechanism applies to other realistic disequilibrated states.\n\n\"The initial condition was an under-heated Harris current sheet with a temperature T = 0.2Teq where Teq = B0²/(4μ0n0kB) is the Harris equilibrium temperature.\"\nThe paper's central claim is that orbit class transitions are responsible for collisionless current sheet relaxation in general, yet only one specific initial condition is tested. Realistic current sheets in space plasmas can be disequilibrated in many ways: over-heated, with density perturbations, with temperature anisotropy, with guide fields, or with asymmetric configurations. The generalizability of the orbit class transition mechanism to these other cases is not demonstrated. For instance, prior work on thin current sheets has shown that temperature anisotropy [[9]](#citation-list) and guide fields [[10]](#citation-list) significantly affect current sheet structure and bifurcation properties.\n\"The initial temperature was set as one-fifth of the Harris equilibrium temperature, i.e., T = 0.2Teq\"\nChoosing exactly 20% of the equilibrium temperature appears arbitrary. The paper does not explore how the equilibration process depends on the degree of disequilibrium. Whether the same orbit class transitions occur and produce similar bifurcated structures for T = 0.5Teq or T = 0.1Teq, or for over-heated cases with T > Teq, remains unexplored. Understanding this parameter dependence would be crucial for establishing the proposed mechanism as a universal explanation for bifurcated current sheets.\n\nReferences:\n[9] [Sitnov, M. I., Guzdar, P. N. & Swisdak, M. A model of the bifurcated current sheet. Geophys. Res. Lett. 30, 1712 (2003)](https://agupubs.onlinelibrary.wiley.com/doi/10.1029/2003GL017218)\n[10] [Zelenyi, L. M., Malova, H. V., Yu Popov, V., Delcourt, D. & Sharma, A. S. Nonlinear equilibrium structure of thin currents sheets: influence of electron pressure anisotropy. Nonlin. Processes Geophys. 11, 579–587 (2004)](https://npg.copernicus.org/articles/11/579/2004/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|17|GPT|1", "source": "prb", "split": "test", "paper_id": "prb17", "comment": "This paper draws an overgeneralized causal conclusion that orbit-class transitions during collisionless equilibration are the origin of bifurcated current sheets in geospace, despite only demonstrating that bifurcation can arise in a specific, idealized disequilibrated Harris-sheet setup and one-dimensional PIC configuration.\n\nCurrent sheets are ubiquitous plasma structures that play the crucial role of being energy sources for various magnetic phenomena. Although a plethora of current sheet equilibrium solutions have been found, the collisionless process through which a disequilibrated current sheet relaxes or equilibrates remains largely unknown. Here we show, through analyses of phase-space distributions of single-particle orbit classes and particle-in-cell simulations, that collisionless transitions among the orbit classes are responsible for this process. Bifurcated current sheets, which are readily observed in geospace but whose origins remain controversial, are shown to naturally arise from the equilibration process and thus are likely to be the underlying structures in various phenomena; comparisons of spacecraft observations to particle-in-cell simulations support this fact.\nThe quoted abstract does more than claim a mechanism for a particular numerical experiment: it frames bifurcated current sheets as “likely” underlying structures in “various phenomena” based on the presented equilibration scenario. That leap is not justified by the evidence shown in the manuscript, which focuses on an initially under-heated Harris sheet and demonstrates one pathway to bifurcation rather than ruling out alternative pathways. In common practice for space plasma structure-formation claims, one expects either (i) systematic parameter scans showing robustness to key environmental variations, or (ii) multi-event observational validation that constrains competing explanations. The paper does not provide such breadth, so the generality implied by “underlying structures in various phenomena” is not adequately supported. Because the statement is in the abstract, it strongly shapes reader interpretation and should meet a higher evidentiary bar than is demonstrated. As written, it risks being interpreted as establishing primacy rather than plausibility.\nIn summary, the collisionless relaxation process of a disequilibrated current sheet was studied. The process is most naturally understood by orbit class transitions, which were analytically predicted and numerically verified. The relaxation mechanism was identified as the origin of bifurcated current sheets, and the significance of this identification in regards to previous explanations of bifurcated structures was discussed.\nThis summary sentence makes an identification claim (“the origin”) rather than a conditional statement (“a possible origin under specified conditions”). Yet the manuscript’s own setup is narrowly scoped (a specific disequilibrium in a Harris-like reversal, followed by a 1D PIC relaxation), which cannot logically establish that the same mechanism dominates in the diverse magnetotail and magnetopause environments where bifurcation is reported. Strong “origin” language is typically reserved for results that demonstrate necessity (e.g., bifurcation does not occur without the mechanism) and robustness (e.g., across relevant guide fields, normal components, and dynamics), neither of which is shown explicitly here. Even if the mechanism is real and important, the paper’s evidence supports “can generate” rather than “is the origin.” This affects the reliability of the conclusions and how the work will be cited and used by others. Reframing the claim to match what is actually demonstrated would substantially strengthen the paper’s validity.\nThey argued that such structures appear as a local or/and temporal en-hancement of the current density away from the neutral sheet, associated with current sheet thinning and flapping prior to substorm onset. In that case the current sheet bifurcation may not be associated with magnetic reconnection.\nThis external discussion explicitly documents that bifurcated profiles can emerge in association with current-sheet thinning and flapping and, importantly, that bifurcation “may not be associated with magnetic reconnection” in some cases [[1]](#cite1). While the paper under review does not claim reconnection is required, it does assert a specific equilibration pathway as “the origin,” which is in tension with literature emphasizing multiple observationally plausible pathways and transient geometries. The point is not that the present mechanism is wrong, but that the observational literature describes a broader phenomenology than a single causal channel. Therefore, claiming a singular “origin” requires more comprehensive evidence than presented. The external quote supports the criticism that the paper’s generalization exceeds what is established by its limited model and comparison. This matters for validity because causal attribution in magnetotail current-sheet morphology is known to be multi-factor and context-dependent.\n\nReferences:\n[1] [Runov, A. et al. *Local structure of the magnetotail current sheet: 2001 Cluster observations.* Annales Geophysicae 24, 247–262 (2006).](https://angeo.copernicus.org/articles/24/247/2006/angeo-24-247-2006.pdf)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|17|GPT|2", "source": "prb", "split": "test", "paper_id": "prb17", "comment": "This paper’s observational validation (the MMS–PIC comparison used to support the bifurcation-origin claim) is not robust because it relies on a single time interval and explicitly omits a spacecraft that does not show bifurcation, while still presenting the agreement as striking evidence for the proposed mechanism.\n\nMMS data and local LMN coordinates Data from MMS2, MMS3, and MMS4 from 20:24:00 to 20:24:15 UT on June 17, 2017 were averaged to yield the profiles shown in Figs. 5a-e. MMS1 data were omitted because the current density did not exhibit an obvious bifurcated structure.\nThis sentence describes a selection step that materially affects the central observational comparison: one of the four MMS spacecraft is excluded specifically because it does not show the target structure. Excluding discordant measurements can be appropriate if there is a prespecified physical reason (e.g., different trajectory through a spatially structured sheet), but the paper does not present such a justification or quantify how omission changes the inferred profile. In current-sheet studies, multi-spacecraft disagreement is often informative about 3D structure, temporal evolution, or crossing geometry; discarding it without analysis can bias conclusions. Because the omitted spacecraft is part of the same tetrahedron, its non-bifurcated current density weakens the claim that the observed sheet robustly matches a bifurcated equilibrium profile. The lack of an uncertainty treatment (e.g., variability across spacecraft) further makes it difficult to judge whether the agreement is meaningful or cosmetic. This directly undermines the strength of the conclusions drawn from Fig. 5.\nApart from such reconnection-related dissimilarities, the observed and simulated profiles agree strikingly well, including the bifurcated current structure.\nThe paper characterizes the agreement as “strikingly well,” which is a strong evaluative statement, yet the comparison is qualitative and is presented for a single short interval. In the same paragraph, the authors acknowledge that the observed current sheet is reconnecting while the simulated one is not, meaning the systems differ in important physics that can affect temperature and pressure tensor structure. Under common validation standards, qualitative similarity in a few profiles is insufficient to support a mechanistic identification without quantitative metrics (e.g., normalized residuals, uncertainty bands) and evidence of robustness across events. The omission of MMS1 (documented elsewhere in the paper) further heightens the risk that the comparison is confirmation-biased. As a result, the “striking” characterization overstates what the evidence can bear. This weakens the reliability of the paper’s interpretation of the MMS event as support for the proposed equilibration mechanism.\nIn examining AE-activity dependence (Table 1) or local plasma conditions we could not find systematic differences between events with different types or different thicknesses of the current sheets in our limited survey. (More focused efforts with a larger database are required to reveal and quan-tify the activity dependence, if it exists at all.)\nThis external statement highlights a key methodological norm for current-sheet morphology claims: robust inference often requires larger event databases and focused statistical efforts [[1]](#cite1). The paper under review instead uses one event as its main observational anchor for a broad mechanistic claim, and even within that event excludes one spacecraft’s measurement. The quoted literature does not invalidate single-event case studies, but it does show that systematic dependence and typology are difficult to establish without broader statistics. Therefore, presenting a single-case qualitative match as strong support (“agree strikingly well”) falls short of common practice for settling an origin controversy. The external quote supports the criticism that the paper’s validation step is underpowered relative to the scope of its conclusion. This is significant because the central claim explicitly targets an unresolved, debated observational phenomenon.\n\nReferences:\n[1] [Runov, A. et al. *Local structure of the magnetotail current sheet: 2001 Cluster observations.* Annales Geophysicae 24, 247–262 (2006).](https://angeo.copernicus.org/articles/24/247/2006/angeo-24-247-2006.pdf)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|17|GPT|3", "source": "prb", "split": "test", "paper_id": "prb17", "comment": "This paper contains a major internal inconsistency in the reported PIC simulation duration (Figure 3 caption versus Methods), which directly affects interpretation of relaxation timescales and prevents precise reproduction of the presented results.\n\nFIG. 3. Streak plots of variables from the particle-in-cell simulation. Streak plots of a the sheared magnetic field \\( B_y \\), b the current density \\( J_z \\), c the ion temperature \\( T_i \\), and d the ion density \\( n_i \\) from \\( t = 0 \\) to \\( 1000 \\omega_{ci}^{-1} \\).\nThis caption states that Fig. 3 spans to \\(1000\\,\\omega_{ci}^{-1}\\), implying a simulation or at least plotted window an order of magnitude longer than what is specified elsewhere. For a relaxation/equilibration study, the time horizon is not cosmetic: it determines whether the shown “equilibrium” is transient, metastable, or persistent. If the figure truly spans \\(1000\\,\\omega_{ci}^{-1}\\), it would also interact with claims about oscillations, damping, or boundary effects over long durations. Conversely, if the correct timespan is \\(100\\,\\omega_{ci}^{-1}\\), then the caption is misleading and the figure may not demonstrate long-term steadiness. Because this is the central simulation evidence for equilibration, ambiguity in the run duration materially weakens confidence in the conclusions. It also prevents others from matching outputs when attempting reproduction.\nThe simulation time was \\(t_{max} = 100\\omega_{ci}^{-1}\\) with a time step \\(\\Delta t = 7.63 \\times 10^{-4}\\omega_{ci}^{-1}\\).\nThe Methods section unambiguously specifies \\(t_{max}=100\\,\\omega_{ci}^{-1}\\), contradicting the Fig. 3 caption’s \\(1000\\,\\omega_{ci}^{-1}\\). This discrepancy cannot be resolved by a reader without access to the authors’ run scripts and plotting code, and it is large enough that it plausibly changes which processes could occur or be visible. In numerical plasma studies, reproducibility depends critically on consistent reporting of domain, timestep, and run duration because these define stability constraints and physical timescales. The paper’s main narrative also references equilibration by \\(\\sim 30\\,\\omega_{ci}^{-1}\\), so clarifying whether the simulation ended at 100 or 1000 affects the evidentiary weight of “remains steady.” A mismatch at this level is a substantive methodology flaw, not a minor typo, because it affects the reader’s ability to interpret and reproduce the central figure. The inconsistency therefore undermines the reliability of the reported simulation-based verification.\nWhenever a result may be of potential interest, keep track of how it was produced.\nThis guidance reflects a widely accepted computational-research norm that the provenance of results must be precisely recorded [[2]](#cite2). The inconsistency between caption and Methods indicates that the paper does not meet this basic standard for at least one of its key simulation outputs. In a field where many details (normalization, timestep, boundary handling, duration) affect results, ambiguous reporting makes independent verification substantially harder. This is especially consequential here because the paper’s primary claims hinge on time evolution (relaxation and equilibration) rather than static equilibria alone. The quote is not a policy statement; it is a methodological requirement to maintain validity of computational claims. The paper’s conflicting time reporting violates this expectation and is therefore a significant issue for reproducibility and interpretation. Correcting and reconciling these reported parameters is necessary for the work to be reliably assessed.\n\nReferences:\n[2] [Sandve, G. K. et al. *Ten Simple Rules for Reproducible Computational Research.* PLOS Computational Biology (2013).](https://journals.plos.org/ploscompbiol/article?id=10.1371/journal.pcbi.1003285)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|17|GPT|4", "source": "prb", "split": "test", "paper_id": "prb17", "comment": "This paper does not provide sufficient materials to reproduce its principal results (orbit-class population analyses and MMS comparison) because it withholds the analysis code (“upon reasonable request”) and the provided code directory is essentially an upstream dependency (PySPEDAS) rather than the paper-specific scripts needed to regenerate the figures.\n\nThe codes used in the data analyses are available from Y.D.Y. upon reasonable request.\nThis sentence establishes that the figure-generation and analysis scripts are not publicly available at publication time. In computational and data-driven plasma-physics studies, the ability to rerun the exact processing steps (including data cleaning, coordinate transforms, averaging, and plotting choices) is essential for independent reproduction and error-checking. “Upon reasonable request” creates a discretionary access barrier and is not equivalent to durable, archival availability, especially as contact details, institutional access, or responsiveness can change over time. This is particularly problematic here because the paper’s key conclusions depend on detailed phase-space diagnostics and a qualitative MMS–PIC match; small processing differences can change inferred structure. The paper does provide raw data locations, but without the scripts that map raw data to the reported profiles, full reproduction is not feasible. This therefore constitutes a major methodology transparency gap.\n```toml\n[project]\nname = \"pyspedas\"\nversion = \"2.0.5\"\ndescription = \"Python Space Physics Environment Data Analysis Software (pySPEDAS)\"\n```\nThis project metadata shows that the bundled “code” is the PySPEDAS package rather than paper-specific analysis scripts. PySPEDAS is a general-purpose community framework and, by itself, does not encode the exact event selection, averaging windows, coordinate definitions, smoothing choices, or plotting steps that produce Fig. 5 and related results. Therefore, including PySPEDAS does not resolve the reproducibility problem created by withholding the authors’ own scripts. In practice, the critical missing artifact is the executable workflow that ties MMS data retrieval and processing to the plotted profiles, along with any scripts used to compute orbit-class diagnostics from simulation outputs. Without those scripts, independent researchers cannot verify whether the reported profiles are robust to reasonable analysis choices. The code block supports the criticism by demonstrating a mismatch between “code availability” needs and the material actually provided. This mismatch directly impacts reproducibility of the central claims.\nThe Python-based Space Physics Environment Data Analysis Software (PySPEDAS) framework supports multi-mission, multi-instrument retrieval, analysis, and visualization of heliophysics time series data.\nThis external description clarifies that PySPEDAS is an analysis framework, not a complete reproduction package for a specific paper’s figures [[5]](#cite5). The existence of a framework does not substitute for sharing the exact scripts and parameters used in a particular study, because frameworks are intentionally flexible and support many alternative workflows. For the manuscript under review, the crucial missing information is how the authors used PySPEDAS (which routines, which data products, what preprocessing, what averaging, what coordinate transformation details beyond the final LMN vectors). The quote thus supports the criticism that bundling PySPEDAS alone is insufficient for replicating the paper’s figure-level results. This is a major issue because the paper’s main validation step is a figure-level match between MMS and PIC profiles. Without the paper’s scripts, readers cannot distinguish between robust physical agreement and analysis-dependent presentation.\nLast, but not least, all input data, scripts, versions, parameters, and intermediate results should be made publicly and easily accessible.\nThis is a well-established standard for computational reproducibility and directly contradicts a “reasonable request” model for key analysis code [[2]](#cite2). The paper under review does share some data locations, but it does not provide the scripts and parameters required to regenerate its main plots and derived quantities. Because the claimed mechanism is subtle (orbit-class transitions inferred from phase-space structure) and the observational validation is qualitative, independent reproduction is especially important to establish trust. The absence of publicly accessible scripts also hinders downstream reuse, extension, and verification by other groups, which is part of normal scientific practice in computational plasma physics. This quote supports the criticism by articulating what is expected for reproducibility when results depend on computational processing. The gap between this standard and the paper’s actual “code availability” materially affects the work’s reproducibility.\nThey are also, we believe, prerequisites for reproducible computational research: if software is not version controlled, readable, and tested, the chances of its authors (much less anyone else) being able to re-create results are remote. (Source: [[3]](#cite3))\nThis sentence articulates a widely accepted view that software in computational science must be treated as part of the experimental method, not a peripheral convenience. In this manuscript, the core claims (orbit-class population changes and MMS–PIC profile agreement) depend on nontrivial data processing, categorization, and plotting, i.e., on software behaving correctly. Without access to the authors’ analysis scripts, readers cannot check whether numerical choices (binning, smoothing, coordinate transforms, and averaging) could produce the reported structures. This is particularly important because the paper’s interpretive claims hinge on qualitative profile features (“bifurcated current structure,” “central dip,” “density plateau”) that can be sensitive to processing details. Treating software as “apparatus” implies it should be inspectable and verifiable by peers, analogous to how instrument calibration and experimental protocols are shared. The quote therefore supports the criticism that withholding the analysis code undermines the reproducibility and auditability of the work’s central results.\nThe files are in hdf5 format. Refer to https://smileipic.github.io/Smilei/post-processing.html for information on how to post-process the data. (Source: [[4]](#cite4))\nThis dataset description shows that the archived PIC outputs require post-processing steps before they become the paper’s plotted quantities and interpreted diagnostics. While sharing large raw outputs is valuable, it is not sufficient for reproducibility unless the exact post-processing workflow used to compute the paper’s figures is also provided. In this manuscript, the main mechanistic evidence involves phase-space structure and orbit-class interpretation, which depend on how distribution functions and moments are computed and visualized from the simulation outputs. If different reasonable post-processing choices (e.g., bin edges, normalization, integration ranges, or time averaging) lead to different apparent bifurcation or anisotropy patterns, then the conclusions are not independently checkable. The quote also indicates reliance on external documentation for generic post-processing, but the missing component is the paper-specific “glue” code that maps these files to Figs. 3–5 and the associated quantitative claims. Therefore, even with the Zenodo archive, the end-to-end reproduction of key results remains blocked without the authors’ scripts and configuration files.\nDocumentation and metadata describing data products, algorithms, instrument calibrations, validation, and data quality will be provided. (Source: [[6]](#cite6))\nThis statement from the MMS data portal highlights that reproducible MMS analyses depend on knowing precisely which calibrated data products and algorithms were used, not just the mission and instrument names. The manuscript specifies a time interval and mentions averaging and minimum variance analysis, but it does not identify the exact MMS product levels, cadences, or any filtering and resampling steps needed to reproduce current density and pressure/temperature tensor profiles. This matters because MMS has multiple data rates and product variants, and derived quantities (like current density peaks and temperature anisotropy proxies) can depend on these choices. The fact that MMS provides extensive metadata and algorithm documentation underscores that the paper could, in principle, be fully reproducible if it published the exact processing pipeline. Instead, the paper directs readers to public data access while withholding the actual analysis scripts, leaving a critical gap between “data available” and “results reproducible.” The quote therefore supports the criticism that the methodology description is insufficiently complete for independent replication of the MMS-based evidence.\n\nReferences:\n[2] [Sandve, G. K. et al. *Ten Simple Rules for Reproducible Computational Research.* PLOS Computational Biology (2013).](https://journals.plos.org/ploscompbiol/article?id=10.1371/journal.pcbi.1003285)\n[3] [Wilson, G. et al. *Best Practices for Scientific Computing.* PLOS Biology (2014).](https://journals.plos.org/plosbiology/article?id=10.1371/journal.pbio.1001745)\n[4] [Zenodo. *Yoon et al 2021 PIC data* (DOI: 10.5281/zenodo.4607112).](https://doi.org/10.5281/zenodo.4607112)\n[5] [spedas/pyspedas. *Python-based Space Physics Environment Data Analysis Software.*](https://github.com/spedas/pyspedas)\n[6] [MMS Science Data Center. *MMS public data site.*](https://lasp.colorado.edu/mms/sdc/public/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|17|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb17", "comment": "The comparison between the 1D non-reconnecting simulation and the MMS event is invalid because the MMS event is undergoing reconnection, which is known to generate bifurcated structures independently of the proposed relaxation mechanism.\n\n\"The finite electron outflow $v_{eL}$ in Fig. 5b indicates that the observed current sheet is undergoing magnetic reconnection, whereas the simulated current sheet, being one-dimensional, is not.\"\nThe authors explicitly acknowledge that the observed event exhibits reconnection signatures (outflow), which are absent in the 1D simulation. This fundamental difference in physical regimes undermines the validity of the comparison.\n\"A sharp peak in the reconnection rate... and a bifurcated current sheet... are also characteristic features of fast kinetic reconnection... [Hesse et al., 1999]\" [1]\nLiterature establishes that magnetic reconnection itself generates bifurcated current sheets (e.g., due to Hall physics and meandering orbits in the diffusion region). Since the MMS event is reconnecting, the observed bifurcation can be plausibly attributed to reconnection dynamics rather than the pre-reconnection relaxation process proposed by the authors. The paper fails to distinguish between these two causes or demonstrate why the relaxation model is a better fit than a reconnection model.\n\nReferences:\n[1] [Ma, Z. W., & Bhattacharjee, A. (2001). Multiscale modeling of magnetospheric reconnection. Journal of Geophysical Research: Space Physics.](https://deepblue.lib.umich.edu/bitstream/handle/2027.42/95438/jgra18824.pdf?sequence=1)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|17|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb17", "comment": "The \"relaxed equilibrium\" obtained in the 1D simulation is likely unstable to 2D instabilities (e.g., tearing, drift-kink) which are artificially suppressed in the simulation, making the equilibrium physically unrealizable or transient in real systems.\n\n\"The 1D simulation domain was $10\\lambda$... periodic boundary conditions were imposed for the fields in the y-direction... The simulated current sheet, being one-dimensional, is not [reconnecting].\"\nThe 1D setup enforces translational invariance in the $y$ and $z$ directions, artificially suppressing tearing modes (reconnection) and drift-kink instabilities.\n\"With recent 3D kinetic simulation results, Ricci et al. (2004) excluded the action of reconnection as the bifurcation trigger, but privileged the role of current aligned instabilities like the lower-hybrid drift instability or the Kelvin-Helmholtz instability.\" [2]\nPrevious studies indicate that current sheets are subject to various 2D/3D instabilities that can alter their structure or lead to bifurcation. By restricting the simulation to 1D, the paper ignores these dominant modes. In a real 3D system, the sheet might succumb to tearing or kinking before or during the proposed relaxation, rendering the \"1D equilibrium\" irrelevant.\n\nReferences:\n[2] [Ricci, P., Lapenta, G., & Brackbill, J. U. (2004). Bifurcated current sheet: Model and observations. Geophysical Research Letters.](https://hal.science/hal-00269295v1/document)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|17|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb17", "comment": "The arguments the authors give and the numerical simulations presented are convincing and novel but, it is not a priori evident for a non-expert why the subject is important to others in the space and/or plasma physics community. I would recommend that the authors address this question with more care before publication so the results can be appealing to a broad audience.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|17|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb17", "comment": "Regarding the comparison between the simulation and the MMS observations. The authors mention that the current sheet observed by MMS is significantly thinner than in the simulation. Can the authors expand on this difference? Is the current sheet close to equilibrium? Does reconnection contribute to thinning the current sheet?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|17|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb17", "comment": "On the same note, the authors should clarify how the x-axes on the two sides in Figure 5 compare. Since the speed and thickness of this current sheet are known from before (i.e., Wang et al., 2020), it should be possible to provide a conversion factor between seconds and “x/lambda” in the observations.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|17|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb17", "comment": "It would be more illustrative if the color scale in Figure 4d & 4i was centered around zero (so that 0 is white).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|17|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb17", "comment": "Line 195: It seems the variable \\\"Re\\\" for Earth radius is not explained.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|17|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb17", "comment": "Line 199: It seems the variable “de” for electron skin depth is not explained.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|17|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb17", "comment": "Line 238: “It fact” -> “In fact”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|18|Claude|1", "source": "prb", "split": "test", "paper_id": "prb18", "comment": "The paper compares simulation results of a 1D static equilibrium relaxation to MMS observations of an actively reconnecting current sheet, which represents fundamentally different physical regimes that undermine the claimed \"universality\" of mixed equilibria.\n\n\"Because the measured sheet is reconnecting, it is not in such static equilibrium as the simulated sheet.\"\nThe authors explicitly acknowledge that the observed sheet is undergoing magnetic reconnection while the simulated sheet is in static equilibrium. Magnetic reconnection involves continuous energy dissipation, topological reconfiguration of field lines, and steady plasma outflows—none of which are present in the equilibration process of a disequilibrated sheet. This fundamental difference in physical regimes raises questions about whether the profile similarities arise from the same underlying physics or are merely coincidental.\n\"However, it is evident from our results that many features of 1D current sheet equilibration apply to 2D reconnecting sheets as well.\"\nThis statement is presented as a conclusion without quantitative support. The paper does not provide any systematic analysis demonstrating that 1D equilibration features carry over to 2D reconnection dynamics. Magnetic reconnection fundamentally changes the current sheet structure through processes like tearing instability, formation of X-lines, and generation of reconnection jets—features absent in simple equilibrium relaxation [1].\n\"While the global veL reversal in Fig. 6b would most likely be interpreted according to the status quo as electron outflows during reconnection, it can also be interpreted as the result of current sheet relaxation leading to guide field amplification as in the present study.\"\nThe authors present an alternative interpretation for electron velocity reversals but do not provide any discriminating analysis to distinguish between reconnection outflows and equilibration-induced shearing. In reconnection, electron outflows are causally linked to the breaking of magnetic field lines at the X-point [2], whereas in equilibration they arise from orbit class transitions. These are distinct physical mechanisms that would require detailed kinetic analysis to differentiate, which is not provided.\n\nReferences:\n[1] M. Yamada, R. Kulsrud, and H. Ji, \"Magnetic reconnection,\" Reviews of Modern Physics 82, 603-664 (2010). https://doi.org/10.1103/RevModPhys.82.603\n[2] J. L. Burch et al., \"Electron-scale measurements of magnetic reconnection in space,\" Science 352, aaf2939 (2016). https://doi.org/10.1126/science.aaf2939", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|18|Claude|2", "source": "prb", "split": "test", "paper_id": "prb18", "comment": "The paper claims \"universality of mixed equilibria\" based on comparison to a single MMS observation from July 3, 2017, which is insufficient to establish general applicability across diverse magnetospheric conditions.\n\n\"The universality of such equilibria is delineated by comparing the simulated current sheet to that observed in space.\"\nThe abstract presents universality as a key conclusion, but this claim rests on a single observational example. Magnetospheric current sheets exhibit enormous variability in thickness, guide field strength, plasma beta, temperature anisotropy, and other parameters. A single event cannot capture this variability. Statistical MMS studies of current sheets, such as those examining multiple electron diffusion regions [3], routinely analyze tens to hundreds of events to establish generalizable conclusions.\n\"Finally, the equilibrium current sheet from the PIC simulation is compared with a current sheet observed by the Magnetospheric Multiscale (MMS) mission, thereby confirming the theoretical and numerical analyses and demonstrating the universality of mixed equilibria.\"\nThe phrase \"demonstrating the universality\" implies a broadly applicable result, but confirmation from one event provides only an existence proof, not evidence of ubiquity. The cited MMS event from Chen et al. [43] was specifically selected for detailed analysis of reconnection, which may introduce selection bias favoring sheets with certain characteristics. Without a survey of multiple events showing consistent agreement with the mixed equilibrium framework, the universality claim remains unsupported.\n\"The measurement time window translates to 2 s ≃ 200 km [43], which, using the measured electron density ne = 0.45 cm−3, translates to ~25 de.\"\nThe paper uses specific parameters from this single event to establish correspondence with simulations. However, these parameters (density, sheet thickness, guide field strength) can vary by orders of magnitude across different magnetospheric regions and solar wind conditions. A comprehensive demonstration of universality would require showing that mixed equilibria emerge across this parameter space.\n\nReferences:\n[3] R. B. Torbert et al., \"Electron-scale dynamics of the diffusion region during symmetric magnetic reconnection in space,\" Science 362, 1391-1395 (2018). https://doi.org/10.1126/science.aat2998", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|18|Claude|3", "source": "prb", "split": "test", "paper_id": "prb18", "comment": "The paper's central observational validation relies entirely on visual comparison of profile shapes without providing any quantitative measures of agreement such as correlation coefficients, chi-squared statistics, or error analysis.\n\n\"Aside from these particulars, the profiles of the measured and simulated sheets agree very well.\"\nThis assessment of \"very well\" agreement is entirely qualitative and subjective. In plasma physics comparisons between simulations and observations, standard practice involves computing quantitative goodness-of-fit metrics [4]. The profiles shown in Figure 6 display notable differences: the simulated TeMM shows a clear double-peak structure while the observed TeMM appears more asymmetric; the density profiles have different functional forms; and the pressure tensor components show systematic offsets. Without quantitative metrics, the claimed agreement cannot be objectively evaluated.\n\"The dashed lines in Figs. 6g and 6l show analytical solutions that are slightly modified from Eqs. 1 and 2.\"\nThe analytical solutions were adjusted (\"slightly modified\") to match the simulation results, specifically with a modified scale λ' ≃ 0.2λ. However, no fitting procedure is described, and no uncertainty bounds on these parameters are provided. The comparison between modified analytical solutions and simulation data also lacks error bars or confidence intervals on the simulation profiles themselves.\n\"The agreement between the analytical and numerical solution is evident, save some details in the pressure tensor\"\nThe acknowledgment of disagreement \"in the pressure tensor\" is treated as a minor detail, but the pressure tensor is central to the force balance that defines current sheet equilibria. Systematic disagreements in pressure components could indicate that the analytical equilibrium spectrum (Eqs. 1-2) does not fully capture the physics, which is mentioned but not quantified: \"strictly speaking, this means that even Eqs. 1 and 2 do not capture the whole spectrum.\"\n\nReferences:\n[4] J. Birn et al., \"Geospace Environmental Modeling (GEM) Magnetic Reconnection Challenge,\" Journal of Geophysical Research 106, 3715-3719 (2001). https://doi.org/10.1029/1999JA900449", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|18|Claude|4", "source": "prb", "split": "test", "paper_id": "prb18", "comment": "The PIC simulations use a reduced mass ratio (mi/me = 100) and an unrealistically low ratio of light speed to Alfvén speed (c/vA = 2), which may affect the electron dynamics central to the claimed shearing mechanism, and the paper does not quantify the impact of these choices.\n\n\"The mass ratio mi/me = 100.\"\nThe realistic ion-to-electron mass ratio is approximately 1836, which is about 18 times larger than the value used. While reduced mass ratios are common in PIC simulations for computational efficiency, they affect the scale separation between ion and electron dynamics. Since the paper attributes current sheet shearing specifically to electron NC→M transitions, the artificially small mass ratio may enhance electron effects relative to ion effects. Studies of reconnection have shown that mass ratio can affect key features of electron dynamics [5].\n\"A simulation run with c/vA = 2 where vA = B0/√(μ0n0mi) (Extended Data Fig. 3) will mainly be referred to in this paper for clarity of presentation; another run with c/vA = 20 was conducted (Extended Data Fig. 4)\"\nIn Earth's magnetotail, typical values of c/vA are of order 100 or greater. The c/vA = 2 case is highly relativistic in the sense that Alfvén speeds are half the speed of light, which is unrealistic for magnetotail plasmas. Even c/vA = 20 is lower than realistic values. The paper notes that equilibration takes \"~30ωci^-1\" for c/vA = 2 but \"~200ωci^-1\" for c/vA = 20, showing significant dependence on this parameter. The main analysis focuses on the c/vA = 2 case, raising questions about whether conclusions extend to realistic parameters.\n\"The difference in the transition types of ions and electrons arises because the single-well condition (p̄zσ = v̄zσ|x̄=0 > -bg²) is more sensitive to changes in bg for electrons than for ions.\"\nThis explanation for the different orbit class transitions of ions versus electrons depends on the relative thermal velocities of the two species, which scale with √(mi/me). With an artificially reduced mass ratio, the contrast between ion and electron thermal velocities is diminished, potentially altering which particles satisfy the single-well condition and thus which transitions dominate. The paper does not analyze how sensitive this mechanism is to mass ratio.\n\nReferences:\n[5] M. A. Shay et al., \"Electron heating during magnetic reconnection: A simulation scaling study,\" Physics of Plasmas 21, 122902 (2014). https://doi.org/10.1063/1.4904203", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|18|Claude|5", "source": "prb", "split": "test", "paper_id": "prb18", "comment": "The derivation of the condition for double-well motion (Eq. S7) relies on small-x̄ approximations that may break down for particles with large oscillation amplitudes, yet the orbit classification is applied throughout the current sheet.\n\n\"Instead, we can make approximations for small x̄, ln cosh x̄ ≃ x̄²/2 and cosh² x̄ ≃ 1 + x̄².\"\nThese Taylor expansions are accurate only for |x̄| << 1. However, the current sheet extends over several half-widths λ, and particles in the NC and DW classes can oscillate to positions where |x̄| >> 1. At x̄ = 2, for instance, ln cosh(2) ≈ 1.32 while x̄²/2 = 2.0, representing a ~50% error. The derivation of Eq. S7 for the double-well condition relies on these approximations, so the orbit classification criteria may be inaccurate for particles with large oscillation amplitudes.\n\"Condition (ii) now becomes simultaneously satisfying f1(x̄+) > f2(x̄+) and f1(x̄-) < f2(x̄-), which is for small x̄±\"\nThe condition is explicitly stated to apply \"for small x̄±\", but the analysis then proceeds to apply the resulting classification (Eq. S7) globally without discussing the regime of validity. The orbit classification in Figures 3-5 encompasses particles throughout the phase space, including those that do not satisfy the small-amplitude assumption. A more rigorous treatment would either derive exact conditions or quantify errors introduced by the approximations.\n\"The solutions to dχ/dx̄ = 0 are the intercepts between the functions f1(x̄) = bg(p̄y - bgx̄) and f2(x̄) = (p̄z + ln cosh x̄) tanh x̄.\"\nFinding the intercepts analytically requires approximations because f2(x̄) involves transcendental functions. The paper acknowledges this cannot \"be solved in closed form\" but does not provide numerical verification that the approximate classification accurately captures the true orbit classes across the full parameter space relevant to the simulations.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|18|GPT|1", "source": "prb", "split": "test", "paper_id": "prb18", "comment": "This paper makes an overstrong universality claim (Conclusions; Validity) based on a single 1D PIC run and a single MMS interval, and the key “agreement” relies on post-hoc, non-validated adjustments to the analytical/observational comparison rather than an observation-driven, uncertainty-aware validation of the mixed-equilibrium hypothesis.\n\n“Here we present the exact process of equilibrium selection, by analyzing the relaxation process of a disequilibrated current sheet under a finite guide field. It is shown via phase-space analyses and particle-in-cell simulations that the current sheet relaxes in such a way that the guide field is locally amplified, yielding a mixed equilibrium from the spectrum. The universality of such equilibria is delineated by comparing the simulated current sheet to that observed in space.”\nThe authors frame their contribution as both “exact” and “universal,” which implies robustness across parameter regimes and observational instances rather than a single illustrative case. In space plasma research, claims of universality typically require either (i) a parameter study demonstrating invariance of the mechanism over relevant dimensionless numbers, or (ii) an event survey demonstrating consistent occurrence across many current sheets. The paper’s own description indicates that the universality argument rests on one simulation-to-one-event comparison, which is not sufficient to establish generality. This matters because mixed equilibria are expected to depend on upstream β, guide-field strength, temperature anisotropy, and geometry (1D vs 2D/3D), all of which vary substantially in nature. Without demonstrating robustness, the conclusion reads as an extrapolation beyond what is shown.\n“*Comparison to spacecraft observations* In order to show the universality of mixed equilibria, we now compare the final equilibrium obtained in the PIC simulation at \\( t = 100 \\omega_{ci}^{-1} \\) to a reconnecting current sheet measured by the MMS spacecraft from 05:26:41.7 to 05:26:43.7 UT on 3 July 2017, when it was located at \\((-17.6, 3.3, 1.7)\\) \\( R_E \\)—where \\( R_E \\) is the Earth’s radius—in Geocentric Solar Ecliptic (GSE) coordinates while crossing the magnetotail plasma sheet.”\nThis explicitly indicates that the observational support comes from a single, short (≈2 s) interval from one date/time. Single-event agreement can be valuable as a case study, but it cannot establish “universality,” especially when current sheets exhibit large variability across environments (magnetotail vs magnetopause vs solar wind) and across events within the same environment. Moreover, a 2-second interval is particularly vulnerable to transient dynamics, coordinate uncertainty, and measurement noise, which should be quantified when used for model validation. Common practice for claims about prevalence/ubiquity is to use statistical samples large enough to separate systematic effects from event-to-event variability. The manuscript does not provide such a statistical basis while still making a universal claim.\n“Because the measured sheet is reconnecting, it is not in such static equilibrium as the simulated sheet.”\nThis admission undermines the logical structure of using a static 1D equilibrium comparison as confirmatory evidence for an equilibrium-selection mechanism. If the observed structure is not in equilibrium, then matching profiles does not uniquely identify the equilibration pathway; reconnection-driven dynamics, temporal evolution, and 3D effects can generate similar signatures. In observational practice, this motivates either selecting non-reconnecting/quasi-static sheets or explicitly quantifying how reconnection modifies the compared profiles. The paper does not show a sensitivity analysis demonstrating that the compared features are diagnostic of relaxation-driven guide-field amplification rather than reconnection or other processes. Therefore, the observational match cannot carry the inferential weight claimed.\n“The dashed lines in Figs. 6g and 6l show analytical solutions that are slightly modified from Eqs. 1 and 2. Because, in the simulation, a seed guide field of strength 0.15 exists and the current sheet pinches down to a length scale \\( \\lambda' \\simeq 0.2 \\lambda \\), \\( B_M = 0.15 + 0.2 / \\cosh(x/\\lambda') \\) is plotted (purple dashed line in Fig. 6g). The analytical pressure tensor component \\( P_{xx} \\) was re-calculated accordingly and it was also assumed that \\( P_{xx} \\) is distributed equally among all three components, and therefore \\( P_{xx}/3 \\) is plotted (cyan dashed line in Fig. 6l).”\nThese steps introduce additional assumptions (a modified analytic profile, a pinched length scale inferred from the simulation, and an isotropization of a tensor component) to improve visual/qualitative alignment. Such post-hoc adjustments are not validated against independent diagnostics (e.g., direct evaluation of the full pressure tensor structure from MMS and from the simulation) and are not accompanied by uncertainty estimates showing how sensitive the agreement is to these choices. In effect, the comparison becomes partially “fit-for-agreement,” which weakens its role as confirmation of the mixed-equilibrium mechanism. In equilibrium validation against spacecraft data, it is standard to (i) compare directly measured quantities without ad-hoc redistribution assumptions, and (ii) quantify residuals and uncertainties. Without that, the strength of the claimed evidence for universality is substantially overstated.\n“We present a statistical analysis of 1261 magnetotail current sheet crossings by the Acceleration, Re-connection, Turbulence and Electrodynamics of Moon’s Interaction with the Sun (ARTEMIS) mission orbiting the moon (X ∼−60 RE), collected during the entirety of Solar Cy-cle 24.” [[1]](https://arxiv.org/pdf/2309.16194)\nThis illustrates common practice for supporting prevalence claims in current-sheet research: a large event set with explicit selection criteria and quantified occurrence rates. While the reviewed paper’s scientific question differs, it uses the language of “universality/ubiquity,” which is typically grounded in multi-event statistics rather than a single comparison. The contrast highlights that the reviewed manuscript’s empirical basis (one MMS interval) is not commensurate with the breadth of its conclusion. Importantly, the existence of such large-sample studies means the bar for “ubiquitous/universal” claims is well established in the field. The reviewed paper could still make a strong contribution by positioning its MMS comparison as an illustrative consistency check rather than a universality demonstration.\n\nReferences:\n[1] [Kamaletdinov, S. R. et al., “Thin current sheets in the magnetotail at lunar distances: statistics of ARTEMIS observations” (arXiv:2309.16194, 2023)](https://arxiv.org/pdf/2309.16194)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|18|GPT|3", "source": "prb", "split": "test", "paper_id": "prb18", "comment": "The paper’s mechanistic and general claims about guide-field relaxation and equilibrium selection (Validity; Data and methodology) are supported by an overly narrow numerical exploration (single \\(b_g\\), reduced mass ratio, only two \\(c/v_A\\) values, 1D geometry), with no demonstrated robustness across relevant dimensionless parameters.\n\n“*Particle-in-cell verification* In order to verify the conjectural answers, one-dimensional particle-in-cell simulation were conducted. The initial condition was an under-heated Harris current sheet with temperatures \\( T_i = T_e = 0.2T_{eq} \\) where \\( T_{eq} = B_0^2/(4\\mu_0 n_0 k_B) \\) is the Harris equilibrium temperature. The sheet was initially immersed in a uniform seed guide field with strength \\( b_g = 0.15 \\). The initial sheet thickness was \\( \\lambda = 10d_i \\) where \\( d_i \\) is the collisionless ion skin depth, and the mass ratio \\( m_i/m_e = 100 \\). A simulation run with \\( c/v_\\Lambda = 2 \\) where \\( v_\\Lambda = B_0/\\sqrt{\\mu_0 n_0 m_i} \\) (Extended Data Fig. 3) will mainly be referred to in this paper for clarity of presentation; another run with \\( c/v_\\Lambda = 20 \\) was conducted (Extended Data Fig. 4), which exhibits plasma oscillations that damp away without affecting the core relaxation mechanism that is orbit class transitions.”\nThis describes essentially a two-point parameter check for \\(c/v_A\\) at a single guide-field strength and a reduced mass ratio, in a 1D setup. While reduced parameters are often used in PIC, claims about “the comprehensive process” of equilibrium selection under finite guide fields should be supported by robustness checks across guide-field strengths, temperature ratios/β, and (ideally) higher dimensionality where additional instabilities exist. The mechanism invoked (orbit class transitions producing sheared current \\(J_y\\) and amplified \\(B_z\\)) could plausibly depend on these parameters, but the paper does not quantify sensitivity. Referring mainly to one run “for clarity” is fine for exposition, but it is not adequate for the breadth of conclusions drawn. The result is that the numerical evidence supports a specific example rather than a general mechanism.\n“Two simulations were conducted, one with (i) \\(c/v_A = 2\\) (Extended Data Fig. 3) and another with (ii) \\(c/v_A = 20\\) (Extended Data Fig. 4). For case (i), 10,000 particles were placed per cell and the simulation was run for \\(100\\omega_{ci}^{-1}\\) with timestep \\(\\Delta t = 7.63 \\times 10^{-4}\\omega_{ci}^{-1}\\), and for case (ii) 100 particles were placed per cell and the simulation was run for \\(250\\omega_{ci}^{-1}\\) with timestep \\(\\Delta t = 7.63 \\times 10^{-5}\\omega_{ci}^{-1}\\). In both cases, the initial condition was a Harris sheet with the ion and electron temperatures set as one-fifth of the equilibrium temperature, i.e., \\(T_{i,e} = 0.2T_{eq}\\) where \\(T_{eq} = B_0^2/(4\\mu_0 n_0 k_B)\\), and with a uniform seed guide field of strength \\(0.15B_0\\).”\nThis confirms that the simulations do not explore guide-field strength, equilibration distance from equilibrium (beyond the single 0.2\\(T_{eq}\\) choice), or mass ratio effects, and they remain 1D. In collisionless plasma problems, such parameters can change orbit stochasticity thresholds, separatrix structure, and electron/ion contributions to currents and heating. Without a parameter scan, it is difficult to know whether the observed “mixed equilibrium” is generic or a feature of this specific initialization. A minimal robustness demonstration would include varying \\(b_g\\) and showing the same qualitative transitions and final profiles, or demonstrating convergence with increasing \\(m_i/m_e\\). The manuscript does not provide this.\n“proton-electron mass ratio\n\nNumerical value 1836.152 673 426” [[6]](https://www.physics.nist.gov/cgi-bin/cuu/Value?mpsme)\nThis CODATA value highlights that the physical proton–electron mass ratio is \\(m_i/m_e\\approx 1836\\), whereas the paper’s PIC simulation uses \\(m_i/m_e=100\\). Such a reduction compresses the separation between ion and electron kinetic scales and can alter how electrons and ions share responsibility for currents, heating, and pressure balance in collisionless current sheets. Because the paper’s central mechanistic claim attributes heating mainly to ions and pinching/shearing mainly to electrons, it is important to demonstrate that these roles persist under more realistic mass ratios (or to provide a principled scaling argument). The manuscript does not provide a mass-ratio convergence study or any sensitivity analysis demonstrating robustness of the equilibrium-selection outcome to \\(m_i/m_e\\). As a result, the numerical evidence supports the mechanism only in the reduced-parameter regime actually simulated. This limitation materially weakens the generality of the paper’s mechanistic conclusions.\n\nReferences:\n[6] [NIST, “CODATA Value: proton-electron mass ratio” (2022 CODATA recommended value)](https://www.physics.nist.gov/cgi-bin/cuu/Value?mpsme)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|18|GPT|4", "source": "prb", "split": "test", "paper_id": "prb18", "comment": "The paper does not provide sufficient artifacts to reproduce the analyses and figures (Data and methodology; reproducibility), because the “code” directory is a third-party library (pySPEDAS) rather than the authors’ analysis pipeline, and the released simulation data do not include the SMILEI input deck and plotting/postprocessing scripts needed to regenerate the reported results.\n\n“The codes used in the data analyses, written in Python 3.8, are available from Y.D.Y. upon reasonable request.”\n“Available upon reasonable request” is not a reproducible release mechanism, especially for computational studies where exact code versions and parameters determine the results. It prevents independent verification and makes reproduction contingent on author responsiveness and long-term code preservation. In modern computational plasma physics, standard practice is to provide the scripts (or a containerized workflow) used to produce each key figure, including data selection, coordinate transforms, averaging, and plotting. This is particularly important here because the paper relies on phase-space classification and on an observation–simulation comparison, both of which are sensitive to processing choices. The statement therefore indicates a reproducibility gap that directly affects the ability to validate the core claims.\n“The files are in hdf5 format. Refer to https://smileipic.github.io/Smilei/post-processing.html for information on how to post-process the data.” [[4]](https://doi.org/10.5281/zenodo.6395310)\nThis shows that the Zenodo deposit provides raw/derived outputs but not the full computational workflow (e.g., SMILEI input/namelist, diagnostics configuration, and the exact postprocessing scripts used to create the paper’s figures). In practice, HDF5 outputs are not self-describing enough to reproduce published analyses without the corresponding diagnostic definitions and plotting code. The need to “refer to” general post-processing documentation emphasizes that the specific processing steps for this paper are not packaged with the data. This is a significant issue because reproducing the guide-field amplification, orbit-class transition diagnostics, and the MMS comparison requires exact preprocessing choices. Therefore, the public data release alone does not make the work computationally reproducible.\n```toml\n[project]\nname = \"pyspedas\"\nversion = \"2.0.5\"\ndescription = \"Python Space Physics Environment Data Analysis Software (pySPEDAS)\"\n```\nThe code bundle provided with the submission is primarily the pySPEDAS project, which is a general-purpose data-access/analysis framework rather than the authors’ study-specific analysis code. Having pySPEDAS available is useful, but it does not specify how the authors used it (which MMS products, cadence, preprocessing, coordinate transforms, filters, and plotting steps) to generate Fig. 6 and related results. In other words, the presence of this dependency does not substitute for the missing “glue code” that defines the actual analysis pipeline. Reproducibility requires both the tools and the exact scripts/configuration used to orchestrate them. Without those, independent readers cannot regenerate the paper’s central observational comparison.\n“Last, but not least, all input data, scripts, versions, parameters, and intermediate results should be made publicly and easily accessible.” [[5]](https://journals.plos.org/ploscompbiol/article?id=10.1371/journal.pcbi.1003285)\nThis widely cited reproducibility guidance is directly relevant to this paper because its claims hinge on computational pipelines (PIC diagnostics and spacecraft data reduction). The reviewed paper provides some data (Zenodo) and points to tools (SMILEI, pySPEDAS), but it does not provide the study-specific scripts/parameters needed to reproduce the published analyses. This falls short of common expectations for computational reproducibility, especially given that the numerical and observational results are used as confirmatory evidence for the proposed mechanism. The shortcoming is not cosmetic: it prevents verification of key steps such as orbit-class assignment, current-density decomposition, and the MMS–simulation alignment. Consequently, the work’s reproducibility—and therefore the reliability of its conclusions—is materially weakened.\n\nReferences:\n[4] [Zenodo record: “Yoon et al 2022 PIC data” (DOI: 10.5281/zenodo.6395310)](https://doi.org/10.5281/zenodo.6395310)\n[5] [Sandve, G. K. et al., “Ten Simple Rules for Reproducible Computational Research” (PLOS Computational Biology, 2013)](https://journals.plos.org/ploscompbiol/article?id=10.1371/journal.pcbi.1003285)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|18|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb18", "comment": "The paper relies on 1D particle-in-cell (PIC) simulations to demonstrate the relaxation process and equilibrium selection, thereby neglecting 2D and 3D instabilities (such as the drift-kink instability) that are known to grow on timescales comparable to or faster than the reported relaxation time.\n\n\"For the simulation run with \\( c/v_A = 2 \\), it takes \\( \\sim 30\\omega_{ci}^{-1} \\) (Extended Data Fig. 3)... to settle to a new equilibrium\"\nThe authors state that the relaxation process takes approximately 30 ion cyclotron periods. However, this timescale is long enough for other instabilities to develop in a multidimensional system.\n\"drift kink instability [9]\"\nThe paper acknowledges the existence of the drift-kink instability (DKI) in the introduction. However, DKI is a 3D instability (with \\( k_y \\neq 0 \\)) that cannot be captured in 1D simulations.\n\"Two-fluid theory of the drift kink instability [9]\"\nPrevious literature (e.g., Daughton, 1999) has shown that the growth rate of the drift-kink instability in thin current sheets can be a significant fraction of the ion cyclotron frequency (e.g., \\( \\gamma \\sim 0.1 \\Omega_{ci} \\)). This implies that the instability could grow by several e-foldings within the \\( 30\\omega_{ci}^{-1} \\) relaxation time, potentially disrupting the current sheet before it can relax to the proposed \"mixed equilibrium.\" By enforcing 1D symmetry, the authors artificially suppress these competing dynamics, rendering the proposed selection mechanism physically questionable for real 3D systems.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|18|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb18", "comment": "The paper claims to solve the mystery of \"equilibrium selection,\" but the results show that the final equilibrium state is deterministically dependent on the specific initial conditions (seed guide field and pressure imbalance), rather than being a preferred state selected by the system dynamics independent of the initial configuration.\n\n\"Through this relaxation process, any particular equilibrium can be attained given the appropriate initial conditions, that is, the seed guide field strength and the initial difference between the thermal and magnetic pressures.\"\nThis statement explicitly admits that the final state is a function of the initial parameters. This contradicts the implication of \"selection,\" which typically suggests that a system evolves toward a specific attractor state (or a limited set of states) largely independent of the precise starting conditions.\n\"One obvious discrepancy is the central \\( v_{eL} \\) reversal... This is because of the localized dip in \\( B_M \\)... A PIC simulation run with a center-dipped initial guide field was conducted, and its results reproduce the central \\( v_{eL} \\) reversal\"\nThe authors demonstrate that to reproduce the specific features of the observed current sheet (the velocity reversal), they had to fine-tune the initial condition (introducing a dip in the guide field). This further proves that the system retains a memory of the initial profile, and the \"selected\" equilibrium is simply a mapping of the arbitrary initial state, undermining the claim that the paper explains a fundamental selection principle.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|18|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb18", "comment": "The paper claims the \"universality\" of the mixed equilibria based on a comparison with a single MMS spacecraft observation, which is statistically insufficient to support such a broad generalization.\n\n\"Finally, the equilibrium current sheet from the PIC simulation is compared with a current sheet observed by the Magnetospheric Multiscale (MMS) mission, thereby confirming the theoretical and numerical analyses and demonstrating the universality of mixed equilibria.\"\nA single case study cannot demonstrate \"universality.\" The observed agreement could be coincidental or specific to the plasma conditions of that particular event. A statistical survey of current sheets with varying guide fields would be required to substantiate the claim that mixed equilibria are the universal outcome of relaxation.\n\"spacecraft observations seem to indicate that finite guide fields deter the formation of bifurcated current sheets [33–37]\"\nWhile the authors cite statistical studies for the bifurcation issue, their own evidence for the \"mixed equilibrium\" structure relies entirely on the single event shown in Figure 6. This creates a disparity between the strength of the claim and the provided evidence.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|18|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb18", "comment": "The paper fails to provide the specific source code, input files, or scripts used to run the particle-in-cell simulations and generate the results, providing instead a general-purpose library (PySPEDAS) that is unrelated to the simulation core.\n\n\"The particle-in-cell simulations presented here were conducted on the KAIROS computing cluster at Korea Institute of Fusion Energy.\"\nThe manuscript mentions the computing resources but does not provide a link to the simulation code (likely `Smilei` based on reference [47]) or the specific input decks used.\n\"code/pyspedas\"\nThe provided `code` directory contains the source code for `PySPEDAS`, a general Python library for space physics data analysis. It does not contain the specific simulation inputs, configuration files, or analysis scripts required to reproduce the PIC simulation results presented in the paper (e.g., Figures 3, 4, 5). Without these files, the numerical experiments are not reproducible.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|18|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb18", "comment": "Too many unneeded modifiers. These words obsfucate the message of the paper. This makes it incredibly more difficult to read. Words like “are exhaustively classified” should be “are classified”. “in order to fathom the equilibrium” should be “in order to understand the equilibrium” fathom is more than a little “over the top”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|18|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb18", "comment": "Was this study run in 2D or 3D? I assume 2D since you made “out of plane” streak plots, but this is not explicitly stated.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|18|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb18", "comment": "FIG 1 is not clear enough to make sense. Consider more traditional line plots of B and rho as cuts in the YX plane. The arrow widths are nearly impossible to decipher and the pink on pink color choice was just bad. What does it mean when the lines are closer or further apart in d)? Explain this to the reader if you maintain these plots. In the text body below Figure 1 you explain “Fig 1d exhibits a finite dBz/dx that does not exist in the initial state”. How can we see dBz/dx when the only thing shown is B not Bz (which I must assume is total magnetic field strength)? If you do not expect to show dBz/dx in FIG. 1d then you should not refer to it, or refer to the appropriate place.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|18|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb18", "comment": "In FIG. 2, how were the ion orbit trajectories determined? Was this done in 2D or 3D? FIG 2 Do the red (cyan, blue) lines match between column 2 and column 3? How have you defined meandering? How does a meandering (M) orbit differ from the other two? Should there really only be only two kinds of orbits, DW and NC? Why does meandering in this paper appear to have a different meaning than in your previous paper [29]? FIG 2 is confusing. Figures a-b-c make sense. you specified that X is normal to the CS.\\n\\nAm I correct in assuming that:\\n1) z direction is along the CS.\\n2) Y is across the CS.\\n3) that your XYZ would be ZXY in GSE coordinates (tail).\\n\\nAs such Column 2 (d-e-f) shows movement along the CS and Column 3 (g-h-i) across the CS? Am I correct in assuming that particle motion is along the CS (by some means) and across the CS due to the Guide Field?Particles can move in both + and - directions along the current sheet and across the current sheet.\\n\\nIn FIG 2 what decides whether the red, blue or cyan will move: one way or the other (+/-Z) along the CS (d-e-f)?\\n\\nIn FIG 2 what decides whether the red, blue or cyan will move: one way or the other (+/-Y) across the CS (g-h-i)?\\n\\nI see that later you specify subclasses based on the sign of\\n\\n-- Figure 2 The green and magenta colors represent By. I assume the colors are plus and minus but it is not stated. --\\nI retract this initial comment and replace it with: I suggest that you move the By and Bz arrows above the column or give them a white background. Pink on pink and Green on green is very hard to see.\\n\\nWhat is your XYZ coordinate system? It does not seem to be any standard system such as GSE. Also you are comparing XYZ with LMN which is given in reference to GSE. This produces confusion. Please clarify how the LMN coordinate system relates to your XYZ system? I mean in general terms like “along the CS™, perpendicular to the CS™, across the CS™”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|18|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb18", "comment": "FIG 4 FIG 5 the color bars could be a little bit wider. They are difficult to see.\\n\\nFIG 4 the parentheses ger very confusing when you have embedded ((x,yz)). I understand your desire to try and duplicate statements for two rows that are slightly different. Try using e-h {m-p} are respectively the same as a-d, except in (x,vy) {(x,yz)} or similarly [square brackets]. “ei-1 [q-t] Ion current density Jiy [Jiz] obtained by taking the first velocity moment of e-h [m- p].”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|18|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb18", "comment": "[Strength of claims] The claim of \\\"universality\\\" that the author makes doesn't seem to be supported enough by the analysis the authors present. In other words, the authors claim that the process they have studied is universal, but the paper does not contain convincing proof of such a statement. For this reason, although the scientific quality of the work is excellent, I don't think that its current version meets the journal requirements.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|18|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb18", "comment": "As it is commonly done in PIC simulations, the authors use a nonrealistic speed of light to Alfvén speed ratio (c/va). The results presented in the Extended Data section show that a larger value of c/va results in the production of waves. The author state that these plasma oscillations damp away without affecting the core relaxation mechanisms. I have a few questions on this point. Which kind of waves are these? Why do they develop when a larger c/va is considered? What dumps these waves? What is the effect of periodicity on the evolution of these waves inside the system? In an open system, would such waves leave the current sheets? Are these waves observed by MMS or any other satellite?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|18|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb18", "comment": "The simulations the authors have performed are 1D. However, the stability of a single current sheet may depend on 3D dynamics. What justifies the 1D approach the authors use? In their conclusions, the authors also admit that in a 2D case they have studied, reconnection spontaneously develops, which makes questionable the existence in natural environments of a 1D equilibrium like what they are presenting in the paper.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|18|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb18", "comment": "Could the authors better explain why the perpendicular electron temperature in their simulation is everywhere larger than the parallel one (Fig 6 panel e-f) while it is the opposite in the observed current sheet? They make an argument on that just before the section \\\"Discussion and outlook\\\"; however, it was hard for me to understand what they mean.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|18|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb18", "comment": "The authors show that their numerical simulations are in accordance with their analysis of particle trajectories. Would it be possible for them to analyze MMS data and extract the VDF for ions and electrons? How do these compare with those obtained from numerical simulations and the analysis of particle orbits?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|18|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb18", "comment": "At the beginning of page 14, the authors note a discrepancy between the analytical and the numerical solution. This discrepancy seems to be a weak point of the paper since the numerical solution does not relax to one of the expected equilibria. Still, it relaxes to some other equilibrium whose analytical form is unknown. It would be a great result if the authors could find an analytical form corresponding to the final state of their simulations.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|18|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb18", "comment": "In their final discussion, the authors claim that mixed equilibria are likely to be ubiquitous. However, they also admit that their MMS observations concern a current sheet out of equilibrium, and this seems an apparent contradiction. Are the type of equilibria discussed by the authors also frequently observed by MMS?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|18|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb18", "comment": "In Fig 4 and Fig 5 a few distribution functions of the kind f(x,v) are plotted. Could the authors specify how the two not plotted velocities are treated? For instance, when vx is plotted, do they plot a particular plane at fixed vy and vz or the average on vy and vz?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|18|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb18", "comment": "I think that the authors should rephrase the last part of their abstract, explaining better what they mean by saying that mixed equilibria are universal.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|19|Claude|1", "source": "prb", "split": "test", "paper_id": "prb19", "comment": "The paper concludes that the observed horizontal polarization \"favours the sustainability of these oscillations by quasi-steady flows\" based on a single event observation, which is insufficient to make general claims about the dominant excitation mechanism of decayless kink oscillations.\n\n\"Simultaneous detection of a 4-min decayless kink oscillation from two non-parallel lines-of-sights, separated by about 104 degrees... reveals, for the first time, a horizontal or weakly oblique linear polarisation of the oscillation.\"\nWhile the detection of polarization from dual vantage points is a valuable methodological advance, the paper presents results from only one oscillating loop bundle observed during a single time interval (09:19 to 10:34 UT on April 1st, 2022). Drawing conclusions about the general excitation mechanism of decayless kink oscillations from this single case is statistically weak. The observed horizontal polarization could be specific to this particular loop or time interval rather than representative of the broader phenomenon.\n\"The revealed polarisation favours the sustainability of these oscillations by quasi-steady flows which may hence supply the energy for coronal heating.\"\nThis strong conclusion about the energy supply mechanism for coronal heating is based on observing horizontal polarization in one event. Even if random footpoint motions could theoretically produce random polarizations, observing horizontal polarization in a single event cannot exclude the possibility that this is simply one realization from a random process. A statistical sample of multiple events showing consistently horizontal polarization would be required to support this conclusion.\n\"Decayless kink oscillations are a common phenomenon in solar coronal loops. Their ubiquity is well supported by the observational results\" from [Anfinogentov, Nakariakov & Nisticò 2015 (A&A, 583, A136)][1]\nThe existing literature, including work by the authors themselves, confirms that decayless kink oscillations are ubiquitous in the solar corona. This ubiquity argues for studying multiple events before making generalizable claims about their excitation mechanism. A single observation showing one particular polarization state cannot characterize the statistics of a \"common phenomenon.\"\n\nReferences:\n[1] [Anfinogentov, S. A., Nakariakov, V. M., & Nisticò, G. (2015). Decayless low-amplitude kink oscillations: a common phenomenon in the solar corona? A&A, 583, A136.](https://ui.adsabs.harvard.edu/abs/2015A%26A...583A.136A)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|19|Claude|2", "source": "prb", "split": "test", "paper_id": "prb19", "comment": "The paper's argument that random footpoint motions should produce randomly polarized oscillations—and therefore the observed horizontal polarization rules out this mechanism—lacks rigorous theoretical foundation and contradicts no established predictions from random-driver models.\n\n\"If the decayless oscillation is sustained by random footpoint movements, the movements are likely to be randomly directed in the horizontal plane. In other words, the horizontal motions are not likely to have a prescribed direction which could be anyhow connected with the orientation of the plane of the loop. Thus, we expect that random, in the horizontal direction, motions of footpoints should result in randomly polarised oscillatory motions of the loop.\"\nThis argument is qualitative and speculative. The theoretical work on random-driver models for decayless kink oscillations, such as Ruderman & Petrukhin (2021), does not make explicit predictions about the resulting polarization distribution. The loop's geometry, density structure, and magnetic configuration could preferentially amplify certain polarization directions even with random footpoint driving.\n\"This picture is inconsistent with the observed behaviour.\"\nThe paper observes horizontal polarization in one event and concludes this is \"inconsistent\" with random driving. However, if random driving produces randomly polarized oscillations, then any specific polarization (horizontal, vertical, or oblique) has some probability of occurring. Observing horizontal polarization once does not contradict a random distribution—it merely represents one sample from that distribution.\nFrom [Ruderman & Petrukhin (2021) MNRAS, 501, 3017–3029][2]: \"We derive the relation between the power spectra of the fundamental mode and all overtones and the power spectrum of the driver.\"\nThe theoretical framework for random-driver excitation of decayless kink oscillations focuses on spectral properties and amplitudes, not on polarization. The authors' claim that random driving produces \"randomly varying polarisation\" is an assumption rather than a derived prediction from established theory.\n\nReferences:\n[2] [Ruderman, M. S., & Petrukhin, N. S. (2021). Excitation of decayless kink oscillations by random motion. MNRAS, 501, 3017–3029.](https://academic.oup.com/mnras/article/501/2/3017/6032187)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|19|Claude|3", "source": "prb", "split": "test", "paper_id": "prb19", "comment": "The paper does not provide formal error bars or confidence intervals on the key measured quantity—the phase difference between oscillations observed from two lines-of-sight—nor does it perform error propagation to assess uncertainties in the polarization classification.\n\n\"The cross-correlation coefficient peaks at a time lag of -0.48 periods, indicating a phase shift of 174 degrees.\"\nThe paper reports a specific phase shift value (174 degrees) without error bars. Given that the light travel time correction (325.5 seconds = 5.4 minutes) is comparable to the oscillation period (4 minutes), small errors in this correction could significantly affect the phase determination. No uncertainty analysis is provided for how measurement noise, loop identification uncertainties, or time calibration errors propagate to the final polarization classification.\n\"The average length of the minor axes, σ, is estimated by the width (standard deviation) of the best fitted Gaussian, resulting in σ = 0.19.\"\nThe parameter σ is presented as a measure of hodogram ellipse elongation, but its uncertainty is not quantified. Furthermore, the paper does not explain how the difference between σ = 0.19 (unfiltered) and σ = 0.08 (filtered) relates to measurement uncertainty versus signal processing effects. The filtered value is used to conclude linear polarization, but this narrow band filtering could artificially reduce the apparent scatter.\n\"As the phase comparison requires the adjustment of the time scales, the light travel time correction is applied to the AIA signal, allowing us to account for the difference in the distances from the Sun to the spacecraft.\"\nThe correction of 325.5 seconds is stated without uncertainty, yet this value depends on the precise orbital positions of both spacecraft. Any systematic error in this correction directly affects the measured phase relationship, which is the primary basis for polarization determination. The paper should have discussed the precision of the spacecraft ephemeris data and propagated these uncertainties.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|19|GPT|1", "source": "prb", "split": "test", "paper_id": "prb19", "comment": "The paper’s central determination of (near) anti-phase behaviour and an “elliptical hodogram” as evidence for horizontal/oblique linear polarisation is not methodologically secured because the analysis pipeline applies motion magnification, envelope normalisation, and narrow-band filtering without demonstrating that these steps preserve the relative phase between the two instruments for this event.\n\n“However, the oscillations were clearly detected in a movie processed with the motion magnification technique (Supplementary Movie 1, right).”\nThis sentence shows that the AIA detection relies on a nontrivial transformation of the data rather than direct measurement from the original sequence. Because the key polarisation result depends on cross-instrument phase relations, any processing that changes temporal phase or introduces lag can bias the inferred polarisation. The paper does not report any validation that the chosen magnification settings leave the phase relationships intact for the specific cadence/noise regime here. In particular, the AIA signal is described as not resolvable “by naked eye” without magnification, which increases the risk that the subsequent phase analysis is effectively performed on a processed proxy rather than the raw observable. Standard practice when drawing physical conclusions from processed signals is to demonstrate phase fidelity via synthetic injections or a controlled test on the same pipeline. Without that, the causal link from “processed movie” to “true oscillation phase” remains insufficiently supported.\n“In addition, the instantaneous amplitudes are normalized by their envelope, to remove the amplitude modulation.”\nEnvelope normalisation changes the time series in an amplitude-dependent way and can distort the relationship between components when the envelope is noisy or estimated with a window comparable to the oscillation period. Because the hodogram shape and phase delay are then interpreted physically, it matters whether this normalisation alters the apparent ellipticity or the timing of extrema. The manuscript does not specify the envelope estimation method, its windowing, or how sensitive the derived 174–180° phase shift is to these choices. In similar time-series analyses, authors typically show that results are stable to reasonable variations of detrending/envelope parameters. Here the absence of such stability checks makes the polarisation inference less secure. This is a major issue because the work’s primary novelty is precisely the polarisation determination.\n“To get rid of the undesired noisy fluctuations beside the 4-min oscillation, we filter out the time-series data with peak frequency with a 30-s window, resulting in cleaner oscillatory signals, as displayed in Fig. 4b. Similar to the original signals, the filtered oscillatory signals detected with AIA and HRIEUV appear to be out of phase with each other. The cross-correlation coefficient peaks at a time lag of -0.48 periods, indicating a phase shift of 174 degrees.”\nThis explicitly ties the headline phase estimate to a specific narrow-band filtering choice (“30-s window”). Narrow-band filters can introduce frequency-dependent phase shifts unless they are constructed to be zero-phase (e.g., forward–backward filtering) and even then can reshape the time series near boundaries. The paper does not specify the filter type, whether it is causal/zero-phase, or how edge effects were handled, yet it reports a phase delay with degree-level precision. Moreover, the polarisation discrimination is stated to hinge on hodogram “width” and phase delay, both of which are sensitive to filtering choices when the signal-to-noise ratio is low. A robust analysis would report uncertainty bands over plausible filter parameters or demonstrate the same conclusion from multiple independent estimators (e.g., Fourier-domain phase, wavelet coherence). Because those checks are not presented, the validity of the polarisation conclusion is weakened.\nThe following code from the supplied motion magnification implementation:\n\n```python\ndef flattop_filter1d(data,width, axis = 0, mode = 'reflect'):\n    window_size =  round(width/0.2327)\n    window = signal.flattop(window_size)\n    window = window/np.sum(window)\n    result = ndimage.convolve1d(data, window, axis = axis, mode = 'reflect')\n    return(result)\n```\nThis code shows that the magnification pipeline explicitly applies temporal convolution (“convolve1d”) with a window whose size is determined by a hard-coded conversion factor. Convolution is a smoothing operation that can alter temporal phase relationships depending on the window and boundary mode, especially when combined with later operations that modify phase increments. The paper’s Methods describe smoothing “over a user-defined width” but do not document this conversion constant, the implied units, or how it relates to the data cadence used for AIA/HRIEUV. When the core scientific claim is a measured phase difference near 180°, undocumented temporal filtering details become critical. This is particularly important because the manuscript treats the hodogram geometry as a diagnostic for polarisation type. The gap between the described method and the specific implementation details undermines confidence in the reported phase-based signatures.\n“We find that for many combinations of viewing and loop geometry it is not straightforward to distinguish between at least two types of kink modes just using time series of images.” [[2]](https://arxiv.org/abs/0808.0685)\nThis statement from prior literature underscores that imaging-only discrimination of kink-mode geometry/polarisation is often ambiguous due to projection and viewing effects. The present manuscript’s discrimination hinges on subtle hodogram properties and phase relations derived from processed imaging sequences, which is precisely the regime where ambiguity can arise. The cited work also highlights that additional constraints (e.g., Doppler signatures) can be needed for unique identification, whereas the current paper relies on a single stereoscopic event plus forward modelling assumptions. Given this known ambiguity, the paper should provide stronger methodological validation that its processing and modelling yield a unique polarisation inference. Without such validation, the claim of “unambiguous” (or effectively decisive) polarisation identification is not sufficiently supported. This affects the validity of the main contribution.\n\nReferences:\n[2] [Wang, T. J., Solanki, S. K. & Selwa, M. “Identification of different types of kink modes in coronal loops: principles and application to TRACE results.” arXiv:0808.0685 (2008).](https://arxiv.org/abs/0808.0685)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|19|GPT|2", "source": "prb", "split": "test", "paper_id": "prb19", "comment": "The paper’s conclusion that the inferred horizontal/oblique polarisation “favours” quasi-steady flows over random footpoint motions is not robust because it is drawn from a single event and rests on an assumption that random drivers should yield randomly varying polarisation, without ruling out alternative models that can reproduce decayless oscillation properties.\n\n“The revealed polarisation favours the sustainability of these oscillations by quasi-steady flows which may hence supply the energy for coronal heating.”\nThis sentence elevates the polarisation inference into an argument for a specific energy-supply mechanism and even a coronal-heating implication. However, the paper analyses one oscillating loop bundle during one interval, so it cannot establish that the inferred polarisation is generic of decayless oscillations or diagnostic of a universal driver. Even if the polarisation for this event is correct, translating that into a preference for quasi-steady flows requires demonstrating that competing mechanisms cannot plausibly yield the same observational signatures. The manuscript does not quantitatively compare likelihoods across proposed drivers, nor does it show that a random-footpoint model cannot produce sustained, stable polarisation for a given loop geometry. In the broader literature, the driving mechanism question is explicitly unresolved, so strong causal language (“favours”) needs correspondingly strong discriminating evidence. As written, the conclusion goes beyond what the presented data and modelling uniquely support.\n“Thus, we expect that random, in the horizontal direction, motions of footpoints should result in randomly polarised oscillatory motions of the loop. This picture is inconsistent with the observed behaviour.”\nThis is the key inferential step used to dismiss random-footpoint driving, but it is asserted rather than demonstrated with a model that maps random forcing to observable polarisation statistics under the event’s specific geometry and line-of-sight configuration. In a resonator, random forcing can still preferentially excite specific eigenmodes, and the observed polarisation can be influenced by loop geometry and projection. The paper does not quantify what “randomly polarised” should mean for the measured hodogram statistics, nor does it provide a null distribution to test inconsistency. Because the claimed inconsistency underpins the mechanistic conclusion, the lack of a rigorous comparison makes the conclusion fragile. A more standard approach would be to simulate random drivers and propagate them through the same observational pipeline to see whether stable near-horizontal hodograms can arise by chance. Without that, the dismissal is not well-justified.\n“However, no definitive answer has yet been given on the driving mechanism behind these oscillations, with most studies focusing on the use of periodic footpoint drivers as a means to excite them.” [[3]](https://arxiv.org/abs/2007.13402)\nThis external statement reflects the field’s current uncertainty regarding decayless-oscillation drivers, highlighting that multiple mechanisms remain plausible. The present paper’s mechanistic inference is therefore operating in a context where strong claims require especially careful exclusion of alternatives. Importantly, the same cited abstract frames self-sustained oscillations as a “proof-of-concept,” implying that even the flow-driven scenario is not uniquely established observationally. Given this context, concluding that one specific mechanism is favoured from a single polarisation measurement should be presented with stronger caveats and quantitative discrimination. The current manuscript instead presents the inference in a comparatively definitive manner. This mismatch between evidential strength and conclusion strength affects the reliability of the paper’s interpretation.\n“We study the mechanism of random excitation of decay-less transverse oscillations of coronal loops. With a spatially one-dimensional and time-dependent analytical model taking into account effects of the wave damping and kink speed variation along the loop, we consider transverse loop oscillations driven by random motions of footpoints. The obtained results successfully reproduce the observed properties of decay-less oscillations.” [[4]](https://arxiv.org/abs/1912.07980)\nThis quote demonstrates that random-footpoint driving is not merely a speculative idea but has been modelled to reproduce key observational phenomenology of decayless oscillations. While it does not directly settle polarisation, it shows that random drivers can produce quasi-monochromatic, eigenmode-dominated signals, weakening the paper’s assumption that randomness must manifest as random observed polarisation. Because the current manuscript uses that assumption to argue against random driving, it should reconcile its argument with the existence of successful random-driver models. A rigorous driver inference would compare the polarisation statistics predicted by such random-driver models (after projection and processing) to those observed. The paper does not do this, so the mechanistic “favouring” claim is under-supported. This undermines the robustness of the conclusions about energy supply.\n“We present an alternative model of coronal-loop oscillations which considers that the waves are trapped in a 2D waveguide formed by the entire arcade of field lines. Further, the oscillatory signal arising from a localized, short-duration source can be interpreted as a pattern of interference fringes produced by waves that have traveled diverse routes of various pathlengths through the waveguide. The rapid decay of this wave component, which has previously been attributed to physical damping mechanisms that remove energy from resonant oscillations, occurs as a natural consequence of the interference process without the need for local dissipation.” [[5]](https://arxiv.org/abs/1312.1922)\nThis provides a concrete alternative explanation for decayless-like behaviour that does not rely on quasi-steady flows sustaining a single-loop oscillator. If interference patterns or arcade-scale waveguiding can generate apparent decayless signatures, then polarisation and phase relations seen in a particular loop bundle may not map uniquely onto a local driving mechanism. The current manuscript mentions interference as an “alternative mechanism” in the introduction but does not assess whether such a model could be compatible with its stereoscopic signatures. Without an explicit comparison, concluding that quasi-steady flows are favoured is premature. The existence of multiple viable frameworks in the literature implies that stronger discriminants are needed. This affects the interpretation of the paper’s main physical implication.\n\nReferences:\n[3] [Karampelas, K. & Van Doorsselaere, T. “Generating Transverse Loop Oscillations through a Steady-flow Driver.” arXiv:2007.13402 (2020).](https://arxiv.org/abs/2007.13402)\n[4] [Afanashev, A. N., Van Doorsselaere, T. & Nakariakov, V. M. “Excitation of decay-less transverse oscillations of coronal loops by random motions.” arXiv:1912.07980 (2020).](https://arxiv.org/abs/1912.07980)\n[5] [Hindman, B. W. & Jain, R. “An Interpretation of Flare-induced and Decayless Coronal-loop Oscillations as Interference Patterns.” arXiv:1312.1922 (2014).](https://arxiv.org/abs/1312.1922)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|19|GPT|3", "source": "prb", "split": "test", "paper_id": "prb19", "comment": "The paper does not provide sufficient materials to reproduce the central forward-modelling comparison and the magnified AIA measurements, because synthetic images are not released and the supplied motion-magnification code lacks version pinning and contains implementation choices that can prevent execution in common environments.\n\n“The artificial images are available from the authors upon request.”\nThe polarisation determination is explicitly based on comparing observations to “forward modelling,” and the figures include “simulated time–distance maps” and “mutual hodograms” used to exclude/retain polarisation types. If the synthetic image sequences (or at least the full parameter sets and scripts that generate them) are not publicly released, independent researchers cannot verify that the reported signatures are reproducible or that alternative parameter choices do not change the conclusions. “Upon request” is a weaker standard than community norms for computational reproducibility, particularly for a claim framed as “for the first time.” This is not a minor convenience issue: the modelling outputs are part of the core evidential chain. Moreover, the absence of released synthetic datasets makes it hard to test sensitivity to loop geometry, viewing angles, and noise, all of which can affect hodogram shape. As a result, the paper’s main inference cannot be independently rederived from the provided artefacts.\n“The magnification factor is within 5-10 depending on the original and desired amplitude.”\nThis indicates that the analysis uses user-chosen hyperparameters that directly change the transformed data used for detection and possibly measurement. For reproducibility, such choices should be made explicit for the exact dataset used in the main results, ideally with scripts or configuration files. The manuscript does not specify the exact magnification factor and smoothing width used for the phase/hodogram analysis (beyond a caption noting coefficient 5 for certain TD plots), nor does it provide a pipeline that reproduces the processed sequences. Because the AIA oscillations are described as not visible without magnification, the reported measurements depend critically on these settings. In reproducible computational workflows, parameter settings are recorded in a machine-readable way and shared. The current presentation does not meet that standard.\nThe following code from the supplied motion magnification implementation:\n\n```python\ndef flattop_filter1d(data,width, axis = 0, mode = 'reflect'):\n    window_size =  round(width/0.2327)\n    window = signal.flattop(window_size)\n    window = window/np.sum(window)\n    result = ndimage.convolve1d(data, window, axis = axis, mode = 'reflect')\n    return(result)\n```\nThis code depends on a specific SciPy API surface (“signal.flattop”) and a hard-coded constant (0.2327) that is not documented in the paper. Without explicit version pinning, such calls can break or change behavior across environments, which directly affects whether other researchers can run the same pipeline. The hard-coded constant also suggests an implicit assumption about units or cadence conversion that is not transparent from the manuscript. In practice, reproducibility requires specifying library versions (or a lockfile/container) and documenting any constants that encode instrument-specific timing. Because the motion magnification step is central to detecting the AIA oscillation, fragility in this code directly undermines the ability to reproduce the observational evidence. This is a substantive reproducibility flaw, not a cosmetic code-quality issue.\nThe following code from the supplied FITS helper:\n\n```python\ndef magnify_fits(input_dir, output_dir, k =4, width=70):\n    print(\"Reading data...\", end = ' ', flush = 1)\n    data, headers, file_names =read_fits_from_dir(input_dir)\n    print('DONE')\n    data_mag = magnify_motions_2d(data, k = 4., width = 70)\n    print(\"writing data...\", end = ' ', flush = 1)\n    save_fits_to_dir(data_mag, headers, output_dir, file_names)\n    print('DONE')\n```\nThis snippet shows that user inputs (`k`, `width`) are not actually passed through to the magnification call, which is hard-coded to `k = 4., width = 70`. Even if this helper script is not the one used in the paper, it illustrates that the distributed tooling is not reliably parameterized and therefore risks divergence between documented settings and executed settings. For a paper where the magnification factor is stated to vary (5–10) and affects detectability, such a discrepancy is material. It also complicates independent replication because one cannot assume that command-line parameters reproduce the authors’ settings. Robust scientific code typically avoids such silent overrides. This further weakens the reproducibility of the reported AIA-based measurements.\n“The tests performed on the artificial data cubes imitating exponentially decaying, multi-periodic and frequency-modulated kink oscillations of coronal loops showed the effectiveness, reliability and robustness of this technique.” [[1]](https://arxiv.org/abs/1611.01790)\nThis sentence from the motion-magnification literature highlights a standard expectation: reliability claims are supported by explicit tests on controlled, artificial data. In the present paper, the motion-magnification step is essential for the AIA detection yet the paper does not provide comparable event-specific test artefacts (e.g., injected synthetic oscillations at AIA cadence/noise) and does not release the relevant synthetic or processed outputs. Given that the cited literature emphasizes testing, the current “upon request” data availability and partial code release fall short of established practice. This is not about adopting every possible best practice, but about providing the minimal information needed to reproduce the main figure-level evidence. Because the central conclusion depends on these transformed data, insufficient reproducibility is a major concern. It affects whether the result can be independently validated.\n\nReferences:\n[1] [Anfinogentov, S. & Nakariakov, V. M. “Motion magnification in coronal seismology.” arXiv:1611.01790 (2016).](https://arxiv.org/abs/1611.01790)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|19|GPT|5", "source": "prb", "split": "test", "paper_id": "prb19", "comment": "The forward-modelling comparison used to discriminate polarisation types is not sufficiently validated against observational complexities (multi-strand bundle structure, line-of-sight intensity integration, partial visibility/overlap), so the mapping from measured hodogram signatures to intrinsic polarisation may not be unique.\n\n“As shown in Supplementary Movie 1, the oscillating loop bundle consists of multiple strands which perform a collective transverse oscillation. Therefore, rather than analysing a specific strand, we treat the bundle as a single entity.”\nThis establishes that the object of analysis is not a single isolated loop but a multi-strand bundle, which complicates the interpretation of measured displacements. In optically thin emission, multiple strands and background structures can contribute to the intensity profile used for Gaussian fitting, potentially shifting the inferred “centre” or “boundary” in a way that depends on viewing angle. Treating the bundle as a single entity can be pragmatic, but then the forward model should reflect that complexity (e.g., multi-thread emission, blending) if it is used for discriminating subtle polarisation signatures. The manuscript does not show such a validation. Because the polarisation inference relies on small differences in hodogram shape (e.g., skewness, ellipse width), unmodelled multi-structure effects could plausibly alter those signatures. This reduces confidence that the forward-model mapping is unique.\n“In AIA images (Fig. 2c and Supplementary Movie 1, middle), the footpoints and one leg are well visible, but some segments of the oscillating bundle are overlapped with bright plasma flows in the background most of the time.”\nThis sentence acknowledges significant background contamination in one of the two key viewpoints. Background flows and evolving intensity structures can affect time–distance maps and Gaussian fits, potentially introducing apparent displacements or phase shifts unrelated to true loop motion. The forward model, however, is purely geometrical and focuses on boundary displacements, without modelling time-dependent background contamination. When one viewpoint is substantially more contaminated, differences between the two measured time series can include systematic observational artefacts that mimic phase differences. A robust forward-modelling comparison would quantify how such contamination affects the hodogram statistics or would restrict analysis to intervals/locations with demonstrably stable backgrounds. Because this is not done, the discriminative power attributed to the hodogram shapes may be overstated.\n“In the model described, the effects of optical depth are omitted, as we focus on the transverse displacements of the loop boundaries only (as kink oscillations are usually observed).”\nIn EUV coronal imaging, intensity is an optically thin line-of-sight integral, and apparent loop position can be affected by column-depth effects and background/foreground structures. Omitting these effects may be reasonable for a first-order study of large-amplitude displacements, but this paper relies on low-amplitude, near-subpixel motions (especially in AIA) and on subtle hodogram morphology. In that regime, intensity-weighted centroid/boundary estimation can be sensitive to line-of-sight emissivity variations and to projection-dependent path length changes. The omission therefore risks a model–data mismatch precisely in the quantities used for discrimination. The paper does not demonstrate that including optically thin intensity formation would not change the simulated hodogram axis ratios or skewness. This limits the validity of the model-based exclusion of polarisation types.\n“We find that for many combinations of viewing and loop geometry it is not straightforward to distinguish between at least two types of kink modes just using time series of images.” [[2]](https://arxiv.org/abs/0808.0685)\nThis literature result directly cautions that geometric forward models and imaging signatures alone can lead to non-unique mode identification across viewing geometries. The current manuscript similarly uses a geometrical model and imaging-based diagnostics (time–distance displacements and hodograms) to infer polarisation type. Given that ambiguity is known to occur, it is especially important to demonstrate that the specific observational complexities in the event (bundle structure, background flows, partial visibility) do not reintroduce degeneracies between polarisation hypotheses. The paper does not provide such a degeneracy analysis or parameter sensitivity study. Therefore, the forward-model-based mapping from hodogram features to polarisation remains insufficiently justified. This affects the validity of the polarisation determination.\n\nReferences:\n[2] [Wang, T. J., Solanki, S. K. & Selwa, M. “Identification of different types of kink modes in coronal loops: principles and application to TRACE results.” arXiv:0808.0685 (2008).](https://arxiv.org/abs/0808.0685)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|19|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb19", "comment": "The paper asserts that the observed horizontal polarization favors \"quasi-steady flows\" as the excitation mechanism, but fails to provide evidence or reasoning for why alternative mechanisms, specifically random footpoint motions, are excluded.\n\n\"The revealed polarisation favours the sustainability of these oscillations by quasi-steady flows which may hence supply the energy for coronal heating.\"\nThis is the main conclusion of the paper regarding the energy source.\n\"The mechanisms which could counteract the oscillation damping are random footpoint movements... and quasi-steady flows\"\nThe authors acknowledge random footpoint movements as a competing hypothesis.\n\"Excitation of decay-less transverse oscillations of coronal loops by random motions [18]\"\nRandom footpoint motions (e.g., granular buffeting) are predominantly horizontal. The paper does not explain why such random horizontal driving would not also produce the observed horizontal polarization. Without demonstrating that random driving produces a *different* polarization signature (e.g., random or circular), the observation of horizontal polarization does not uniquely favor quasi-steady flows.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|19|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb19", "comment": "The paper reports a peak in the cross-correlation coefficient to support the anti-phase relationship but fails to report the actual value of the coefficient, making it impossible to assess the statistical significance of the result.\n\n\"The cross-correlation coefficient calculated with different time lags peaks at a time lag of 120 s, almost exactly at half of the oscillation period (4 min).\"\nThe text mentions the lag time but omits the correlation coefficient value.\n\"The cross-correlation coefficient peaks at a time lag of -0.48 periods, indicating a phase shift of 174 degrees.\"\nAgain, the peak value is missing. Given that the AIA signal is \"not resolvable by naked eye\" and requires motion magnification, the signal-to-noise ratio is a major concern. A low correlation coefficient would undermine the claim of a coherent oscillation between the two instruments, yet this critical statistic is absent.", "reviewer_type": "ai", "label": "error", "error_type": "Neglect", "label_origin": "expert+llm-filter"}
{"id": "prb|19|Gemini|5", "source": "prb", "split": "test", "paper_id": "prb19", "comment": "The study relies heavily on Motion Magnification to detect oscillations in the AIA data and determine their phase, but does not validate whether this image processing technique preserves the precise phase information required for the analysis.\n\n\"oscillations recorded by AIA are not resolvable by naked eye... clearly detected in a movie processed with the motion magnification technique\"\nThe AIA detection is entirely dependent on this technique.\n\"The method magnifies the displacement amplitude linearly... without changing the oscillation period.\"\nWhile the authors claim amplitude and period preservation, they do not demonstrate that the *phase* relative to an external reference is preserved with the accuracy needed to distinguish 180 degrees from other shifts. In low signal-to-noise regimes, complex wavelet transforms can introduce phase artifacts. A control experiment using synthetic data with known phase shifts and noise would be necessary to validate the method's suitability for this specific phase-sensitive application.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|19|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb19", "comment": "With only one example it is difficult to generalise the finding. The polarisation of the motions is likely to depend on other factors, such as the geometry of the loop. In the absence of a general pattern derived from observations involving more cases, it is difficult to establish a firm conclusion about the implication of the finding for the excitation mechanism/coronal heating.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|19|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb19", "comment": "My main concern with this work is with one of the assumptions that the authors made during the analysis. In particular, I am refering to the assumption of considering the frequency fluctuations in the observed oscillatory signals as the result of noise. This is strongly connected to both major conclusions of this study. 1) Section 2.2, lines 148-150: 'The average length of the minor axes... where 0.7 is the half width of the major axis'.\\nSection 2.3, lines 183-187: For the circular polarisation... with the axes ratio 0.45 in the phase portrait'.\\nSection 2.4, lines 204-209: 'However, only models with... or another origin'.\\nSection 3, lines 226-228: 'We conclude that the detected kink mode... with a strong horizontal component'.\\n\\n-- From the analytical model we see that the elliptical trajectory in the hodogram gives a ratio of minor to major axes of 0.6 for the circular polarisation and 0.45 for the elliptical polarisation, while it leads to a very narrow line-like structure for horizontal and oblique polarisations. From the observations, the authors find a minor to major axes ratio of 0.27 for the observed time series and a ratio of 0.11 for the filtered time series. Based on the latter, and after comparing with the hodograms produced for the different polarisations in the analytical model, the authors conclude that the observed oscillation must be linearly polarised with a very strong horizontal component.\\nThe main assumption that led the authors to their conclusion is that the fluctuations in the period of the two unfiltered signals come down to noise, and that this noise must be removed with a filter. However, this fluctuation manifests similarly in both signals, despite the two coming from different instruments with noticeably different spatial resolutions. This could possibly indicate a more intrinsic origin of those fluctuations, such as a more elliptically polarised oscillation. Such an assumption could be supported by comparing the ratio of the unfiltered signal (0.27) and the analytical model (0.45), again taking into account observational uncertainties.\\nI would like the authors to comment on this, and further explain why they believe this fluctuation to be caused by noise. This comment is not meant to remove from the results and the value of authors conclusions. In fact, their assumption about the period fluctuations is very reasonable. I would just like the authors to expand upon their reasoning, and make it more clear both in the text and in their response to the referee.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|19|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb19", "comment": "2) Section 3, lines 242-251: 'If the decayless oscillation is sustained... (or an oblique, but with a large horizontal component) polarisation'.\\n\\n-- This comment is directly connected to the previous major comment, and is about the second main conclusion of this study. Assuming a linear, strongly horizontal polarisation for the decayless oscillation, the authors then make a strong case supporting a self-oscillatory process through the interaction of the loop with steady flows, as the driving force behind the observed oscillation. If this conclusion is correct, then this work potentially addresses one of the main unknowns behind decayless loop oscillations. However, if the oscillation is elliptically polarised, then we cannot exclude the possibility of random footpoint movements driving the oscillation. Random footpoint motions would result in a randomly varying polarisation, but resonance of the loop to the driving should lead to an amplified response to certain frequencies (see Afanashev et al. 2020). The resulting oscillation could still resemble an elliptically polarised one, to a certain extent. I would like for the authors to further expand upon this, either in the text or in their response to the referee.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|19|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb19", "comment": "In the right panel of the Supplementary Movie 1, the date as mentioned in the title of that panel should have be \\\"2022-04-01\\\" rather than \\\"2022-01-01\\\". It would be better to have this fixed.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|19|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb19", "comment": "1. Section 1, line 45-46: 'the ubiquity of decayless kink oscillations makes them an important process for the coronal energy balance.'\\n\\n-- Although it is expected from decayless oscillations to affect the energy balance in the solar atmosphere, the nature and importance of these effects are still under debate. In particular, the energy dissipation mechanism is still not well understood. For example, the concept of steady state KH instability turbulence requires higher-than the observed amplitudes of decayless oscillations to sustain the quiet solar corona (Hillier et al. 2020), or even predicts radiative cooling (see Hillier & Arregui 2019, for oscillating prominence threads). The authors are advised to at briefly mention some of the opposing views on the subject.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|19|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb19", "comment": "3) Section 1, line 59-60: 'So far, there has been only one attempt to estimate the polarisation plane stereoscopically, for a large-amplitude decaying regime'\\n\\n-- In Aschwanden & Schrijver (2011), the authors used a combination of STEREO EUVI/A and SDO/AIA data to estimate stereoscopically the 3D loop shape, as well as the plane of oscillation with respect to the loop plane. They concluded that the observed loop kink oscillation was vertically polarized. The authors should consider rephrasing this and/or include this additional reference.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|19|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb19", "comment": "4) Section 2.3, line 176-177: 'situated near the loop apex (i.e., near the location of the 177 maximum oscillation amplitude).'\\n\\n-- It should be specified that the two slits shown in Figure 5 and considered in Figure 6 technically belong to Leg 2 (for HRIEUV image) and Leg 1 (AIA image) respectively, despite being close to the apex. This way, the authors will avoid causing confusion among the readers, when they compare this sentenced to what is shown in Figures 5 and 6.\\n\\nLike I have already mentioned, this a well written manuscript that is efficiently conveying the results of the current study. It includes a very good analysis with reasonable assumptions and no major flows. I find this work and its conclusions very interesting and I would be happy to read the re-submitted version of it, once it is uploaded.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|21|Claude|2", "source": "prb", "split": "test", "paper_id": "prb21", "comment": "The neutral outflow mass rate of ~100 M☉/yr, which is central to the paper's conclusion that outflows strongly impact star formation, has a stated systematic uncertainty of 0.7 dex (~factor of 5), and additional assumptions that could reduce this value by nearly an order of magnitude, potentially making the outflow rate comparable to rather than dominant over the star formation rate.\n\n\"The systematic uncertainty on this result is dominated by the observed scatter in the dust depletion value, which is 0.5 dex. ... Combined with the uncertainty on the calcium dust depletion, this gives a total uncertainty on the outflow mass of ~0.7 dex, similar to that on the ionized outflow mass (but due to a different set of assumptions).\"\nA 0.7 dex uncertainty means the true neutral outflow mass could be as low as ~20 M☉/yr or as high as ~500 M☉/yr. At the lower end, the outflow rate would be comparable to the residual star formation rate of 1-10 M☉/yr, significantly weakening the claim that \"the outflow is able to substantially affect the star formation rate.\"\n\"If we make the most conservative choice on the systemic component of Na I D and on the outflow radius we obtain a mass outflow rate for the neutral phase that is 8.5 times lower compared to our default assumptions, i.e., Ṁout = 11 M☉/yr.\"\nThe paper acknowledges that under conservative assumptions, the neutral mass outflow rate could be only 11 M☉/yr. This is within the same order of magnitude as the star formation rate upper limits derived from multiple methods (10 M☉/yr from hydrogen recombination lines, 28 M☉/yr from Paγ). At this level, the outflow would not necessarily dominate over star formation, substantially weakening the claim that \"the gas ejection is likely to have a strong impact on the evolution of the galaxy.\"\n\"For consistency with local studies we make the standard assumption 1-y = 0.1, meaning that only 10% of the sodium is in the neutral phase; it is likely that the true value is even lower, which would increase the derived column density and therefore the outflow mass.\"\nWhile the paper notes that lower ionization fractions would increase the outflow mass, this assumption of 1-y = 0.1 is taken from local studies. At z=2.445, the UV radiation field and ionization conditions may differ substantially from local environments, introducing additional uncertainty that is not fully quantified. The direction of systematic bias from this assumption is unclear for high-redshift systems.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|21|Claude|3", "source": "prb", "split": "test", "paper_id": "prb21", "comment": "The paper assumes an electron density of ne = 500 cm⁻³ with a 0.7 dex systematic uncertainty for ionized outflow mass calculations, but recent studies have shown that commonly-used density diagnostics like [S II] ratios can lead to significant systematic errors in outflow mass estimates, and the actual density range in AGN outflows can span several orders of magnitude.\n\n\"The electron density cannot be reliably derived from the flux ratio of the poorly resolved [S II] and [O II] doublets. We make the standard assumption of ne = 500 cm⁻³, however we note that this value is highly uncertain. Since local studies using different methods find a wide range of values, log ne ~ 2 - 3.5, we assign a systematic uncertainty of 0.7 dex (a factor of 5 in each direction) to the assumed value of ne.\"\nThe paper correctly notes the uncertainty in electron density but the assumed range may be insufficient. Davies et al. 2020 (cited as reference [62] in the paper) specifically examined this issue and found that traditional [S II]-based densities can significantly underestimate true electron densities in AGN outflows, potentially by more than an order of magnitude. Higher actual densities would result in lower ionized outflow masses than reported, though the ionized phase is already acknowledged to be subdominant.\n\"We calculate the emissivity for each line using pyNeb with standard assumptions (density 500 cm⁻³ and temperature 10⁴ K).\"\nThe temperature is fixed at 10⁴ K without uncertainty assessment. Temperature variations can affect emissivity calculations significantly. While this is a standard assumption, the outflowing gas may have different thermal properties than typical HII regions, particularly if shock heating is present as suggested by the high outflow velocities.\n\n* Quote from literature: \"Observational tests of this scenario rely on determining outflow masses, which requires measuring the electron density (ne) of ionized gas. However\" (from recent MNRAS article on electron densities in outflows [[2]](#ref2))\nRecent work has highlighted that electron density measurements from traditional forbidden line ratios may systematically overestimate outflow masses. While the paper's ionized outflow mass is already subdominant to the neutral phase, this systematic issue affects the interpretation of the agreement between different ionized line tracers presented as validation of the methodology.\n\nReferences:\n[2] \"Electron densities from [S ii] lines significantly overestimate the...\" MNRAS (2025). [doi:10.1093/mnras/staf2075](https://academic.oup.com/mnras/article-abstract/doi/10.1093/mnras/staf2075/8340368)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|21|Claude|4", "source": "prb", "split": "test", "paper_id": "prb21", "comment": "The paper uses BPT diagram line ratios to argue for AGN activity as the outflow driver, but acknowledges that the emission lines being analyzed trace the outflowing gas rather than the galaxy. Shock excitation from outflows can produce AGN-like line ratios on BPT diagrams, creating a circular argument where the outflow is used to infer AGN activity which is then used to explain the outflow.\n\n\"We note that some of the measured emission lines (notably [O III] and Hβ) trace the outflow rather than the galaxy, which may complicate the interpretation of the position on the BPT diagram.\"\nThe paper correctly identifies this potential complication but does not adequately address it. If the [O III] and Hβ emission primarily traces shocked outflowing gas rather than AGN-photoionized gas, then the BPT classification is measuring properties of the outflow rather than independently confirming an AGN. This creates potential circularity in the argument that AGN activity is driving the outflow.\n\"The line ratios measured in COSMOS-11142 are fully consistent with those measured in the outflows of high-redshift quasars\"\nWhile this comparison supports consistency with AGN-driven outflows, it does not distinguish between photoionization by an AGN and shock excitation. Research has shown that slow to moderate velocity shocks (200-1000 km/s) can produce emission line ratios that fall in the AGN regime of BPT diagrams [[3]](#ref3). The observed outflow velocities in COSMOS-11142 (~600 km/s for neutral gas, up to ~1700 km/s for ionized gas) are within the range where shock excitation could contribute significantly to the line emission.\n\"The only reasonable explanation is therefore that the observed outflow is driven by AGN feedback. This is confirmed by the emission line flux ratios\"\nThe paper presents the BPT classification as confirmation of AGN-driven feedback, but given that the emission lines trace the outflow itself, this reasoning may be partially circular. Alternative confirmation would require independent AGN indicators, but the paper notes the galaxy is undetected in X-ray and radio observations, and mid-infrared colors do not meet AGN selection criteria.\n\nReferences:\n[3] Kewley, L.J., et al. (2013). \"Theoretical Evolution of Optical Strong Lines across Cosmic Time.\" ApJ 774, 100. Referenced in [arXiv:2512.14646](https://arxiv.org/html/2512.14646v1) showing \"galaxies, even with slow shocks (km s⁻¹ to 200 km s⁻¹), can mimic the emission line ratios seen in the transition zone.\"", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|21|GPT|1", "source": "prb", "split": "test", "paper_id": "prb21", "comment": "The manuscript draws a strong causal conclusion that AGN-driven neutral-gas ejection is rapidly suppressing star formation in COSMOS-11142, but the paper’s own quantified uncertainties and alternative interpretations leave the key comparison (neutral-gas mass outflow rate versus residual star formation) insufficiently decisive to support this conclusion.\n\n“We thus conclude that supermassive black holes are able to rapidly suppress star formation in massive galaxies by efficiently ejecting neutral gas.”\nThis sentence makes a strong causal claim (“rapidly suppress”) and specifies a mechanism (“efficiently ejecting neutral gas”), but the paper’s measurements primarily establish kinematics and model-dependent mass outflow rates rather than direct gas removal or suppressed star formation caused by the outflow. In current extragalactic outflow literature, demonstrating quenching typically requires either (i) a direct depletion/removal of the cold-gas reservoir (e.g., molecular gas mass and depletion time), or (ii) spatially resolved evidence that star formation is reduced where the outflow impacts the ISM. Here, the main quantitative argument is the comparison of \n\\(\\dot{M}_{\\mathrm{out}}\\) to SFR, which is highly sensitive to adopted geometry, radius, and absorption-to-column conversions (and the paper acknowledges additional factors beyond its nominal systematic). Because the paper does not measure the molecular gas phase and does not quantify whether the outflow escapes the potential well, the mechanism “ejecting” the relevant star-forming fuel is not established. As a result, the presented evidence supports “presence of an outflow during quenching,” but not the stronger statement that the outflow is the *cause* of rapid quenching via efficient ejection.\n“The neutral mass outflow rate estimated from the Na I D line is 97 \\( M_\\odot/\\mathrm{yr} \\)… If we make the most conservative choice on the systemic component of Na I D and on the outflow radius we obtain a mass outflow rate for the neutral phase that is 8.5 times lower compared to our default assumptions, i.e., \\( \\dot{M}_{\\mathrm{out}} = 11\\ M_\\odot/\\mathrm{yr} \\).”\nThis passage shows that the headline neutral outflow rate can change by nearly an order of magnitude purely from choices about (i) a systemic Na I D component and (ii) the neutral outflow radius—both central to the main causal argument. Once the comparison to the residual SFR is made, this swing can change whether \\(\\dot{M}_{\\mathrm{out}}\\) is “clearly larger” than SFR or only comparable. The paper treats \\(11\\ M_\\odot/\\mathrm{yr}\\) as still “one order of magnitude larger” than the ionized outflow, but the quenching claim hinges on the neutral outflow exceeding the *star formation rate*, not merely exceeding the ionized phase. Because the uncertainty budget is not propagated jointly with SFR uncertainties (and because additional systematics beyond these two choices exist), the causal interpretation is not robust. This is especially important because the paper frames the result as “direct observational evidence” for SMBH-driven quenching, which demands stronger causal support.\n“The Prospector fit gives a star formation rate of \\( \\sim 3\\ M_\\odot/\\text{yr} \\) … we obtain an upper limit of \\( 10\\ M_\\odot/\\text{yr} \\). … we can place a 3-\\(\\sigma\\) upper limit … yielding an upper limit on the star formation of \\( 28\\ M_\\odot/\\text{yr} \\). … COSMOS-11142 is not detected in the *Spitzer* 24-\\(\\mu\\)m observations … yielding a 3-\\(\\sigma\\) upper limit of \\( 38\\ M_\\odot/\\text{yr} \\)….”\nThe manuscript’s own SFR constraints span a wide plausible range, including conservative upper limits that approach or exceed the conservative neutral outflow rate estimate (\\(\\sim 11\\ M_\\odot/\\mathrm{yr}\\)). That means the key diagnostic “\\(\\dot{M}_{\\mathrm{out}} > \\mathrm{SFR}\\)” is not guaranteed under the paper’s own conservative bounds, even before considering additional modeling uncertainties in \\(\\dot{M}_{\\mathrm{out}}\\). In practice, the SFR estimates also mix indicators with different systematics (e.g., recombination lines that can be contaminated by outflow emission, and mid-IR heating biases in quiescent/post-starburst systems). Because the paper does not present a joint probabilistic comparison (posterior for \\(\\dot{M}_{\\mathrm{out}}/\\mathrm{SFR}\\) including all stated systematics), the conclusion that the outflow is “able to strongly suppress” star formation is not statistically secured. This undermines the robustness of the manuscript’s causal interpretation even for this single object.\n“Direct observational evidence for the radiative or quasar mode of feedback, which occurs when the AGN is very luminous, has been difficult to obtain but is accumulating from a few exceptional objects.” [Fabian 2012, hyperlinked citation][1]\nThis review statement summarizes a broad consensus that linking AGN-driven outflows to star-formation termination is observationally challenging and tends to rely on exceptional systems with unusually direct evidence. The paper under review aims to provide such evidence in a high-redshift quenching galaxy, but it does not present direct measurements of the cold-gas reservoir being removed (e.g., molecular gas mass and depletion time) or spatially resolved suppression. Instead, it relies on model-dependent outflow-rate inference and an SFR comparison that is not decisive under conservative assumptions. The juxtaposition highlights a gap between the level of evidence typically required for strong “quenching by feedback” claims and what is delivered here. Citing such a review is relevant because the manuscript’s conclusion is framed in similarly strong terms (“rapidly suppress star formation”), which should meet the higher evidentiary bar. Without additional direct observables, the paper’s conclusion remains suggestive rather than robust.\n\nReferences:\n[1] [A. C. Fabian. “Observational Evidence of AGN Feedback.” arXiv:1204.4114 (2012).](https://arxiv.org/abs/1204.4114v1)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|21|GPT|2", "source": "prb", "split": "test", "paper_id": "prb21", "comment": "The neutral outflow mass and mass outflow rate inferred from Na I D are methodologically fragile because the conversion from equivalent width to column density assumes an optically thin regime and adopts a covering fraction of unity, despite the doublet being unresolved and without an empirical optical-depth constraint—an approach known to be unreliable for Na I D superwind absorption.\n\n“The first step is to derive the Na I and Ca II column density from the observed equivalent widths (listed in Table 1), which can be done easily in the optically thin case [51], yielding \\( N_{\\text{Na I}} = 2.2 \\times 10^{13} \\) cm\\(^{-2}\\)….”\nThis sentence makes explicit that the key Na I column density is obtained via an optically thin equivalent-width conversion. However, Na I D absorption in galactic outflows is frequently saturated/optically thick, and in that regime equivalent width is not linearly proportional to column density. While the paper notes these are “lower limits,” the subsequent steps (ionization correction, depletion, geometry, and radius) treat the derived \\(N_{\\mathrm{NaI}}\\) as a quantitative input for \\(N_{\\mathrm{H}}\\) and \\(\\dot{M}_{\\mathrm{out}}\\), which can impart a false sense of precision. Without resolving the doublet or otherwise constraining optical depth, the mapping from EW to column density can vary by orders of magnitude depending on saturation and velocity structure. This directly affects the claimed neutral dominance and the comparison to SFR that underpins the quenching interpretation. In common practice, Na I D-based outflow mass estimates require careful handling of saturation and partial covering, not a simple optically thin conversion.\n“Unless one can constrain the Ca II or Na I doublet ratio [63], it is only possible to measure the product of the covering fraction and the column density. However, the mass outflow rate only depends on this product, thus making this decomposition unimportant for our analysis. For simplicity, here we assume a covering fraction of unity.”\nThe manuscript acknowledges that the Na I doublet ratio is needed to disentangle covering fraction from column density, but then asserts that this decomposition is “unimportant” because \\(\\dot{M}_{\\mathrm{out}}\\) depends only on the product. That statement is only strictly safe in the optically thin limit where EW tracks \\(C_f N\\) linearly, yet the paper simultaneously warns that small deviations from optically thin can “substantially increase” the inferred column. In the optically thick regime, the observed EW can be dominated by velocity dispersion and covering fraction rather than column density, so \\(C_f N\\) is not uniquely determined without optical-depth information. Assuming \\(C_f=1\\) can therefore bias the inferred column density and propagate into \\(N_H\\) and \\(\\dot{M}_{\\mathrm{out}}\\). The combination of “unresolved doublet” and “covering fraction of unity” is a major methodological vulnerability given how central \\(\\dot{M}_{\\mathrm{out}}\\) is to the conclusions. The paper’s stated 0.7 dex systematic may understate the true uncertainty if the absorption is not in the optically thin regime.\n“The NaD lines are optically-thick… This implies that the absorbing gas does not fully cover the background continuum light… In this circumstance - in which optically-thick gas only partially covers the continuum source - the measured equivalent width of the NaD doublet … will be insensitive to the NaI column density….” [Heckman et al. 2000, hyperlinked citation][2]\nThis literature result directly challenges the assumption that an optically thin EW-to-column conversion yields a meaningful quantitative \\(N_{\\mathrm{NaI}}\\) in superwind-like Na I D absorption. It also emphasizes that partial covering is expected, and that EW may be controlled by covering fraction and kinematics rather than column density in the relevant regime. The paper under review fixes the Na I D doublet ratio to the optically thin value during fitting and then derives \\(N_{\\mathrm{NaI}}\\) from EW “easily in the optically thin case,” which is precisely the regime where Heckman et al. warn the method does not hold for many superwinds. Because the manuscript does not resolve the doublet and does not present an independent saturation/covering analysis (e.g., via higher-resolution data, alternative lines, or radiative-transfer modeling), it cannot demonstrate that its Na I D absorption lies in the optically thin regime where the conversion is valid. This is not a minor technicality: it is the core measurement step for the neutral outflow rate. As a result, the neutral \\(\\dot{M}_{\\mathrm{out}}\\) and any conclusions derived from it remain uncertain beyond what is quantitatively justified.\n\nReferences:\n[2] [T. M. Heckman, M. D. Lehnert, D. K. Strickland, L. Armus. “Absorption-Line Probes of Gas and Dust in Galactic Superwinds.” arXiv:astro-ph/0002526 (2000).](https://arxiv.org/abs/astro-ph/0002526v1)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|21|GPT|3", "source": "prb", "split": "test", "paper_id": "prb21", "comment": "The paper presents the AGN interpretation as effectively confirmed, but the evidence is not decisive because (i) the BPT ratios use lines that the paper itself notes trace the outflow (not the host ISM), (ii) shocks can reproduce AGN-like BPT ratios, and (iii) high-redshift star-forming loci differ from local BPT populations—so “exclusively AGN” is an overstatement for the diagnostic used.\n\n“The presence of an AGN is confirmed by the high [N II]/Hα and [O III]/Hβ line ratios [15].”\nThis statement treats optical line-ratio diagnostics as confirmatory for AGN power, but in outflowing systems the same line ratios can be produced by shock excitation and mixing of multiple gas phases. A key methodological requirement for BPT interpretation is that the line ratios correspond to a physically coherent emitting region; however, the manuscript later notes that some of the relevant lines trace the outflow rather than the galaxy. Without additional diagnostics (e.g., coronal lines, high-ionization UV lines, or spatially resolved separation of galaxy vs outflow emission), calling the AGN “confirmed” is too strong. The paper also reports no X-ray or radio detection, removing two standard independent AGN channels. While AGN may still be present, the presented evidence supports “AGN plausible/likely” rather than “confirmed.” Overstating diagnostic certainty weakens the validity of downstream causal claims about AGN feedback.\n“COSMOS-11142 occupies a region on these Baldwin-Phillips-Terlevich (BPT) diagrams [15] which is exclusively populated by AGN systems. We note that some of the measured emission lines (notably [O III] and H\\( \\beta \\)) trace the outflow rather than the galaxy, which may complicate the interpretation of the position on the BPT diagram.”\nThe paper asserts an “exclusively AGN” region but immediately concedes that the key lines used in the ratio may not trace the same physical component of the galaxy, undermining the interpretability of a single-point placement on the BPT plane. Mixing outflow-dominated [O III]/Hβ with more systemic components (or shocks) can shift line ratios into the nominal AGN region even without an energetically dominant AGN. Moreover, the statement “exclusively populated by AGN systems” is framed relative to local populations, yet high-redshift star-forming galaxies are known to occupy different regions in BPT space than local star formers. The manuscript does not present a redshift-appropriate comparison sample or demarcation that accounts for this evolution. As a result, the BPT-based “exclusively AGN” claim is not supported at the level of generality stated. This overconfidence matters because the AGN-driving premise is used to support the broader feedback/quenching conclusion.\n“the nebular spectra of high redshift star-forming galaxies occupy an almost entirely distinct re-gion of the BPT diagram as compared to local galaxies.” [Steidel et al. 2014, hyperlinked citation][3]\nThis sentence establishes that local BPT occupancy is not directly transferrable to high-redshift systems, weakening any argument that a given BPT region is “exclusively” AGN based on local-galaxy distributions. The reviewed paper explicitly compares COSMOS-11142 to “the local galaxy population” on BPT diagrams and uses that to assert exclusivity. In the presence of strong redshift evolution of nebular conditions, the correct standard is to use high-redshift-calibrated demarcations or comparisons to high-redshift star-forming samples. Otherwise, classification boundaries risk mislabeling high-z star formation, shocks, or composite excitation as AGN. The Steidel et al. statement is widely supported by high-z spectroscopy and is directly relevant to the manuscript’s diagnostic choice at \\(z\\approx2.45\\). Therefore, the paper’s “exclusively AGN” phrasing is not methodologically sound.\n“the shock models produce emission line ratios almost completely overlapping with the AGN models in the BPT…” [Calabrò et al. 2023, hyperlinked citation][4]\nThis directly shows that BPT ratios alone can be degenerate between AGN photoionization and fast-shock excitation, particularly in disturbed/outflowing gas. The manuscript itself acknowledges potential shock contribution by stating that \\(L_{\\mathrm{bol}}\\) inferred from [O III] is “an upper limit since part of the observed line luminosity may come from shock excitation,” which is consistent with the degeneracy described here. When shocks overlap AGN in BPT space, an argument that relies on BPT placement as confirmation is insufficient without additional discriminants. This is especially relevant for an object explicitly exhibiting an outflow with large velocity offsets and broad lines—conditions where shocks are plausible. Therefore, the AGN-driving interpretation should be presented as plausible but not definitively confirmed.\n\nReferences:\n[3] [C. C. Steidel et al. “Strong nebular line ratios in the spectra of z ∼ 2–3 star-forming galaxies: first results from KBSS-MOSFIRE.” arXiv:1405.5473 (2014).](https://arxiv.org/abs/1405.5473v2)\n[4] [A. Calabrò et al. “Near-infrared emission line diagnostics for AGN from the local Universe to z ∼ 3.” arXiv:2306.08605 (2023).](https://arxiv.org/abs/2306.08605v2)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|21|GPT|4", "source": "prb", "split": "test", "paper_id": "prb21", "comment": "The paper’s core results are not reproducible from the provided methods description because crucial steps (JWST reduction modifications, Blue Jay survey reduction specifics, and imaging/photometry modeling via ForcePho) are deferred to “in preparation” works without enough implementation detail, and no code or full processing configuration is provided.\n\n“We reduced the NIRSpec data using a modified version of the JWST Science Calibration Pipeline v1.10.1, using version 1093 of the Calibration Reference Data System. … For more details on the Blue Jay survey and the data reduction, see Belli et al. (in preparation).”\nThis indicates that the reduction is not a standard pipeline run but a “modified version,” which can materially affect extracted spectra, flux calibration, and line measurements—central to the outflow inference. Deferring details to an “in preparation” reference prevents independent reproduction because the modifications, parameters, and QA cuts are unspecified. In observational astrophysics, reproducibility typically requires either (i) a public reduction repository or (ii) a complete description of non-default pipeline steps and parameter settings sufficient for another group to rerun the processing. This paper provides versions but not the actual modifications, which is the key missing element. Since the outflow inference depends on subtle line profiles and continuum subtraction, unreproducible reductions directly threaten the reliability of the reported quantitative values. Therefore, the methodological reporting is insufficient for reproducibility.\n“For the NIRCam data… we fit the surface brightness profile… using Forcepho (Johnson et al., in preparation).”\nStructural parameters (e.g., \\(R_e\\)) are later used in the neutral-outflow radius discussion and thus influence \\(\\dot{M}_{\\mathrm{out}}\\) through \\(R_{\\mathrm{out}}\\) assumptions. By relying on an “in preparation” code/method without a public reference or a complete algorithmic description, the manuscript makes it difficult to reproduce the photometry and morphology measurements. In high-impact JWST-era papers, it is common practice to provide either a public code link, a versioned release, or enough methodological detail (priors, PSF modeling, likelihood, convergence checks) to replicate results with alternative tools. Here, the description is high-level and does not specify ForcePho configuration or validation beyond qualitative residual statements. Because these measurements feed into physical interpretation (e.g., size scale for outflow), this lack of reproducibility is consequential rather than cosmetic. The paper should provide a reproducible pathway for these derived quantities.\n“This package contains the Python software suite for the James Webb Space Telescope (JWST) calibration pipeline… The tools in this package allow users to run and configure the pipeline to custom process their JWST data.” [JWST calibration pipeline documentation, hyperlinked citation][5]\nThe official documentation emphasizes that the pipeline is configurable and can be customized, which implies that non-default configurations can produce different calibrated products. Because the reviewed paper uses a “modified version” of the pipeline, the exact configuration and code changes become essential methodological information. Merely reporting the pipeline version and CRDS mapping is not enough to reproduce a custom processing run, especially for spectroscopy where extraction, background subtraction, and outlier rejection choices can alter weak line wings and kinematics. The documentation supports the point that reproducibility requires specifying how the pipeline was run/configured, not only which version was used. Without such specifics, independent groups cannot verify whether the reported line measurements and derived outflow rates are robust to reasonable pipeline choices. This undermines the transparency and reproducibility expectations for JWST-based quantitative claims.\n\nReferences:\n[5] [JWST calibration pipeline developers. “Package Documentation — jwst (JWST calibration pipeline).”](https://jwst-pipeline.readthedocs.io/en/latest/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|21|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb21", "comment": "The paper assumes that the radius of the neutral gas outflow is identical to that of the ionized gas outflow (~3 kpc) without sufficient observational justification. Given that the neutral gas is detected in absorption against the stellar continuum (which has a half-light radius of only 0.6 kpc), the neutral gas could be located much closer to the galaxy. This assumption directly affects the derived mass outflow rate, potentially overestimating it by nearly an order of magnitude and undermining the conclusion that the outflow is \"massive\" and capable of quenching the galaxy.\n\n\"we assumed that the radius of the neutral outflow coincides with that of the ionized outflow; in principle, the neutral outflow radius could be as small as the galaxy effective radius, which is 0.6 kpc\"\nThe authors acknowledge that the neutral gas radius is unconstrained and could be as small as 0.6 kpc. Since the mass outflow rate scales linearly with the radius (or more strongly depending on the assumed geometry and covering fraction), assuming a radius of 3 kpc instead of 0.6 kpc artificially inflates the mass outflow rate.\n\"If we make the most conservative choice on the systemic component of Na I D and on the outflow radius we obtain a mass outflow rate for the neutral phase that is 8.5 times lower compared to our default assumptions, i.e., \\(\\dot{M}_{\\mathrm{out}} = 11\\ M_\\odot/\\mathrm{yr}\\).\"\nThe authors admit that a conservative estimate yields a rate of 11 \\(M_\\odot\\)/yr, which is significantly lower than their headline figure of ~100 \\(M_\\odot\\)/yr. This lower rate is comparable to the upper limits of the residual star formation rate (10-28 \\(M_\\odot\\)/yr), weakening the claim that the outflow is \"substantially higher\" than the star formation rate and thus the primary driver of quenching.\n\"It cannot be smaller than this because the observed depth of the gas absorption reaches \\(\\sim 50\\%\\) of the stellar continuum, meaning that the neutral gas must be in front of at least 50% of the stars in the galaxy\"\nThis argument only constrains the covering fraction, not the radial distance. A shell of gas at 0.6 kpc can cover 50% of the stars just as well as a shell at 3 kpc, provided the geometry is appropriate. Thus, there is no observational evidence ruling out a compact, lower-mass outflow.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|21|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb21", "comment": "The paper claims that the observed outflow explains the \"rapid quenching\" of the galaxy. However, the dynamical age of the outflow (~10 Myr) is much shorter than the time elapsed since the quenching event (~100-300 Myr, as indicated by the post-starburst spectrum). This temporal mismatch suggests that the observed outflow is a subsequent event (e.g., maintenance mode) rather than the cause of the initial cessation of star formation.\n\n\"The travel time to reach a distance of \\(R_{\\text{out}} \\sim 3\\) kpc at the observed velocity is less than 10 Myr, which is much smaller than the time elapsed since the starburst phase, according to the inferred star formation history.\"\nThe authors explicitly calculate that the outflow is young (< 10 Myr) compared to the post-starburst age. This discrepancy indicates that the starburst had already ceased long before the current outflow was launched.\n\"The rapid quenching of massive galaxies at \\(z > 1\\) may thus be fully explained by the AGN-driven ejection of cold gas.\"\nThis conclusion is not supported by the data for this specific galaxy. While the outflow might prevent rejuvenation, it cannot \"fully explain\" the rapid quenching that occurred ~100 Myr prior to the outflow's launch. The causal link between the *current* outflow and the *past* quenching event is broken by the timeline.\n\"COSMOS-11142 is among the most massive targets... and is one of the 17 objects that are classified as quiescent... The presence of deep Balmer absorption lines clearly indicates that the galaxy is in the “post-starburst” phase immediately following the rapid quenching of a star formation episode.\"\nThe classification as \"post-starburst\" implies a significant delay (typically >100 Myr) after the main burst. The presence of a young outflow in an already quenched galaxy does not prove that the outflow caused the quenching.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|21|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb21", "comment": "The interpretation of the redshifted He I emission line as solely the receding component of the outflow, revealed by resonant scattering, is not sufficiently supported by the data. Resonant scattering in outflows typically produces a P-Cygni profile (blueshifted absorption and redshifted emission). The absence of a reported blueshifted absorption component (or a discussion of why it is missing) makes the \"receding side only\" interpretation speculative.\n\n\"He I is the only emission line that is redshifted (\\(\\Delta v \\sim +400\\) km/s) compared to the systemic velocity of the galaxy, implying that we are seeing the receding side of the outflow but not the approaching side.\"\nThe authors assert that they see only the receding side. In a standard resonant scattering scenario (like Lyman alpha), the approaching side is often visible as absorption (P-Cygni profile) or suppressed emission. The complete absence of the approaching component without a corresponding absorption feature is unusual and requires a more detailed radiative transfer explanation than provided.\n\"This behavior is often found in observations of the Ly\\(\\alpha\\) line, which experiences resonant scattering... Since the He I transition involves a meta-stable level... it can give rise to a similar resonant scattering\"\nWhile the analogy to Lyman alpha is physically motivated, Lyman alpha often shows complex profiles including blueshifted absorption. The authors do not demonstrate that the column density of metastable He I is sufficient to fully absorb the blueshifted emission without producing a detectable absorption trough in the continuum (or if the continuum is too faint, why the emission is fully suppressed).\n\"We do not detect X-ray or radio activity; however the presence of a supermassive black hole is suggested by the properties of the ionized gas emission lines.\"\nGiven the lack of independent confirmation of the AGN properties (e.g., X-ray), relying on a non-standard interpretation of a single emission line (He I) to confirm the outflow geometry is risky. Alternative explanations (e.g., inflow, complex kinematics) should be considered.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|21|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb21", "comment": "The paper argues for the \"strong impact\" of the outflow by comparing the mass outflow rate to the *residual* star formation rate (SFR) of the already-quenched galaxy. To demonstrate that the outflow was capable of *quenching* the galaxy, the relevant comparison should be with the SFR of the galaxy *before* it quenched (the progenitor SFR), which was likely much higher.\n\n\"The mass outflow rate... is larger than the residual star formation rate, indicating that the gas ejection is likely to have a strong impact on the evolution of the galaxy.\"\nComparing the outflow rate (~11-100 \\(M_\\odot\\)/yr) to the residual SFR (<10 \\(M_\\odot\\)/yr) sets a low bar for \"impact\". A massive galaxy at z~2.5 typically has a main-sequence SFR of hundreds of \\(M_\\odot\\)/yr [1]. If the outflow rate is closer to the conservative estimate (11 \\(M_\\odot\\)/yr), it would have been insufficient to quench the main star formation episode.\n\"We then find \\(\\dot{M}_{\\text{out}} \\sim 100 \\, M_\\odot/\\text{yr} \\) for the neutral outflow... However, the mass outflow rate of COSMOS-11142 is an order of magnitude larger than the typical value\"\nEven if the rate is 100 \\(M_\\odot\\)/yr, it must be compared to the SFR during the starburst phase to assess its quenching potential. The current comparison only shows that the outflow can *maintain* quiescence, not that it *caused* it.\n\nReferences:\n[1] Whitaker, K. E. *et al.* Constraining the Low-mass Slope of the Star Formation Sequence at \\(0.5 < z < 2.5\\). *ApJ* **795**, 104 (2014).", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|21|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb21", "comment": "p. 3. The authors use v_out = |delta-v| + 2 sigma, but this expression refers to the maximum outflow velocity, not the \\\"typical\\\" (median) velocity of the outflowing gas. As a consequence, in my opinion, dM/dt is overestimated. The authors should investigate the impact of choosing |delta-v| and/or |delta-v| + 1 sigma, instead of |delta-v| + 2 sigma, as the characteristic outflow velocity on their estimates of dM/dt (and change their conclusions accordingly, if needed).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|21|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb21", "comment": "pp. 5 and 14. The ratio between molecular, neutral-atomic, and warm-ionized mass outflow rates vary widely among local outflows. The ratio of (molecular + neutral-atomic) to (warm-ionized) mass outflow rates is typically large in gas-rich systems (e.g. ULIRGs and dusty quasars; Rupke, Gultekin, & Veilleux 2017), but this ratio is likely lower in gas-poor systems, such as COSMOS-11142, due to a general deficit of cool gas in these systems. I therefore find the statement \\\"the molecular phase (not probed by our observations) is expected to be equally effective as the neutral phase at ejecting gas\\\" to be rather optimistic given that COSMOS-11142 is gas-poor and with an unknown amount of molecular gas. I suggest to tone it down. Similarly, the assumption on p. 14 that \\\"the neutral phase is comparable to the molecular phase\\\" is fraught with large uncertainties.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|21|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb21", "comment": "pp. 6 and 14. The lack of X-ray and radio detection of the AGN in this object is somewhat intriguing given the inferred (upper limit on the) AGN bolometric luminosity, log L_bol ~ 45.3. Possible explanations should be briefly mentioned.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|21|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb21", "comment": "pp. 7, 8, and ff. As shown in Fig. 4, the MSA microshutters of NIRSpec miss a significant fraction of the galaxy, including part of the nucleus. The authors estimate on p. 8 that the slit-loss correction is ~ 2. However, this estimate is based on photometric measurements. I worry that this correction could be more severe when considering quantities that are derived from the absorption and emission line features, such as the outflow properties (velocity, column, mass, etc), since the line emission and absorption associated with the outflow may not be homogeneous and distributed spherically symmetrically around the nucleus. The authors should address this issue and possibly add it in their measurement uncertainties.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|21|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb21", "comment": "p. 8. The stellar mass, log M*/Msun = 10.9, reported on this page is missing an uncertainty. This makes it hard to judge whether the discrepancy discussed later on pp. 8-9 between dynamical and stellar masses is significant. The authors should quantify this discrepancy given the uncertainties (e.g. \\\"...different at the N-sigma level\\\"...)", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|21|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb21", "comment": "p. 10. To explain that Halpha appears to be slightly blueshifted compared to [N II], the authors speculate that perhaps \\\"Halpha mostly comes from the outflow while [N II] originates in the galaxy\\\". This statement is hard to justify given that both features trace warm ionized gas, unless the excitation, density, or metallicity is also different between these two regions. The authors should clarify what they have in mind here.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|21|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb21", "comment": "p. 13. The authors should be more explicit and state that the \\\"canonical value\\\" used for dust depletion refers to the Milky Way value and let the readers judge if it is a reasonable assumption here.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|21|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb21", "comment": "p. 14 and Fig. 9 caption. The authors should replace all statements about the \\\"Baldwin-Phillips-Terlevich (BPT) diagrams\\\" with the \\\"standard optical diagnostic diagrams of BPT and Veilleux & Osterbrock (1987)\\\" since the [S II] diagram they use for their analysis was first introduced in 1987 by Veilleux & Osterbrock (the spectra of BPT did not extend far enough to the red to include the [S II] doublet).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|21|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb21", "comment": "While these data showcase the possibility of JWST for this work, I'm not convinced that it should be published in Nature. The science is interesting within the niche of establishing neutral gas outflow properties in post-starburst galaxies, but its broader appeal would be limited. Furthermore, the data itself has limitations: the result is primarily based on an optical spectrum of relatively low spectral and spatial resolution. The analysis of this spectrum needs improvement, but I'm not convinced the data will allow the improvements required to address uncertainties in the line fitting. Better data is available from, e.g., the NIRSpec IFU mode of JWST with higher-resolution gratings. A paper on a very similar galaxy to this one, in fact, has just been submitted to arXiv and Nature Astronomy, but with the benefit of IFU data (arXiv:2308.06317). I thus suggest that Nature Astronomy or ApJ Letters would be a more appropriate venue for this result.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|21|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb21", "comment": "The line fitting is not presented in enough detail to assess its quality. Each line is fit separately, but the signal-to-noise and spectral resolution are low so it is hard to assess whether the fits to individual lines are really robust, even as presented in Figures 2, 6, and 7. Certainly at higher resolution some of these lines would break up into multiple components, and even now the data seem to point to a second blueshifted component in [OII] and [OIII], at least judging from Figures 1 anad 8. Some of the fits are not correct, such as near [SII] where it appears the stellar model underfits the continuum, leading to more flux in the emission lines. A better correction needs to be applied here. There is no limit on at least one important diagnostic line, [OI] 6300 A, typically used in line ratio diagrams to assess ionization and excitation. I notice lines present that are not fit, such as the [NI] 5198/5200 doublet. In general, I am skeptical that the emission lines should show so much differences from each other in kinematics; e.g., that Halpha should be blueshifted by so much.\\n\\nThe authors should at least attempt a global fit of all lines, or at least define 2 or 3 groups of lines to fit together with similar kinematics. This would provide better constraints on the weak lines, but also on strong lines with degeneracies (e.g., Halpha due to the strength of [NII]).\\n\\nI am consequently concerned about the estimate of Mdot from different species. That assumes a lot about the gas ionization and other uncertainties in different species. It is most reliable to use Balmer lines, which don't require such corrections (except for density).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|21|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb21", "comment": "Dust. The interpretation of the emission lines, particularly [SIII] and Hel, given in Figure 1 and the text is based primarily on arguments around dust obscuration. For this to be robust, it would need to be quantified using a wavelength-dependent extinction curve. Furthermore, there needs to be discussion of the gas extinction based on observed ionized emission lines. The authors currently seem to rely on extrapolation from stellar extinction in the SED model (which I assume includes the usual correction from stellar to gas color excess; Calzetti et al. 2000).\\n\\nThe fits to [NII] and [SIII] seem very similar, so I don't think [SIII] has its shape due to differential dust attenuation. There are two [SIII] lines -- do they yield the same result?\\n\\nThe Hel is interesting, and I like the interpretation -- have the authors double-checked for wavelength calibration issues?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|21|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb21", "comment": "Velocities. The manuscript uses more-or-less a \\\"maximum\\\" velocity as the bulk velocity of the gas. But most of the gas, as detected, is at the central velocity of each line. This is what is appropriate for calculating mass outflow rates. There may be some unresolved projection effects, though not in the model as presented. Thus the outflow rates will be lower by a factor of a few.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|21|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb21", "comment": "Size. It is not obvious from Figure 8 that the highly-blueshifted [OIII] line is spatially-resolved. The size the manuscript suggests appears to use the size of the less blueshifted part of the line. This circles back to the point about line fitting above -- are there constraints on the spatial extent of the other observed lines? Are there two outflows here, one lower-velocity, spatially resolved and one high-velocity, unresolved?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|21|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb21", "comment": "Presence of an AGN. The presence of an AGN is inferred from the galaxy's position on the line ratio diagrams in Figure 9. However, the only contextualization is comparison to low-z galaxies, for which this system appears as an extreme outlier. A robust comparison to recent results on both high-z star-forming galaxies and AGN is warranted. Galaxies shift on these diagrams with increasing redshift. Simply comparing to low-z data and models is insufficient.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|21|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb21", "comment": "Covering fraction. The covering fraction can in fact be determined from the existing data; see, e.g., the formulae in Section 4.3 of Hamann et al. 1997, ApJ, 478, 80.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|21|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb21", "comment": "Absorption line fitting: The model for Call shown in Figure 6 does not look like a 2-to-1 optical depth ratio -- it would be better to fix it to 2, or at the very least set that as an upper limit for the ratio, since it physically can't be larger than that in the optically-thin limit.\\n\\nThe authors assume that Nal is optically thin based on Call. However, Nal is typically mildly optically thick when observed in these contexts. Call H and K are not usually observed, so the fact that the gas is dense enough to detect it suggests that Nal is even more likely to be optically thick. (The difference in detection rate presumably arises due to the large difference in dust depletion, given that they have similar oscillator strengths.) A fit with the line ratio allowed to vary would be more appropriate. If in fact the optical depth is higher, the covering factor may differ from unity. The optical depth and blueshift of NaI D may also be a lower and upper limit, respectively, if in fact there is redshifted resonant emission that is filling in the red side of the absorption line. The presence of redshifted HeI could suggest that such emission is a real possibility.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|21|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb21", "comment": "Please quantify the statement \\\"relatively weak emission lines\\\" as a indicator of quiescence. At issue is really the equivalent width of the Balmer emission lines. Similarly, the manuscript states that the \\\"deep Balmer absorption lines clearly indicates that the galaxy is in the 'post-starburst' phase.\\\" Again, the indicator is this combined with low Balmer emission line equivalent width, quantifiably.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|Claude|1", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "The paper claims to model how specific molecular mechanisms of anesthesia (GABA-A potentiation and NMDA blockade) affect whole-brain dynamics, but the whole-brain simulations simultaneously change both synaptic time constants and spike-frequency adaptation parameters, conflating molecular drug effects with neuromodulatory adaptation changes.\n\n\"In the whole-brain model, \\( b_e = 5\\)pA and \\( \\tau_e = 5\\)ms in AI, \\( b_e = 30\\)pA and \\( \\tau_e = 3.75\\)ms in synchronous state\" (Figure 4 caption, describing NMDA-blocker simulation)\nThe simulation that is claimed to model NMDA blockers (ketamine) simultaneously changes \\( \\tau_e \\) from 5ms to 3.75ms AND \\( b_e \\) from 5pA to 30pA. This represents a 6-fold increase in adaptation current alongside the synaptic time constant change. Since NMDA blockers like ketamine do not directly modulate spike-frequency adaptation (which is controlled by neuromodulators like acetylcholine), this parameter combination does not specifically model the molecular mechanism of ketamine. Rather, it conflates two distinct mechanisms, undermining the claim that the framework isolates molecular-level drug actions.\n\"In the whole-brain model, \\( b_e = 5\\)pA and \\( \\tau_e = 5\\)ms in AI, \\( b_e = 30\\)pA and \\( \\tau_i = 7\\)ms in synchronous state\" (Figure 4 caption, describing GABA-ergic simulation)\nSimilarly, the GABA-ergic anesthesia simulation (modeling propofol) simultaneously changes both \\( \\tau_i \\) (from 5ms to 7ms) and \\( b_e \\) (from 5pA to 30pA). This conflates the direct molecular action of propofol on GABA-A receptors with adaptation current changes. The paper explicitly states that \"Variations in the level of acetylcholine are also observed for anesthetics such as propofol but it does not constitute its main pharmacological effect,\" yet the simulations require adaptation changes to produce the desired dynamics, contradicting the stated aim of modeling molecular-specific mechanisms.\n\"Here, we address this issue by presenting a computational approach for brain simulations using biophysically grounded mean-field models that integrate membrane conductances and synaptic receptors, showcased in the example of anesthesia.\"\nThe abstract claims the approach integrates specific membrane conductances and synaptic receptors. However, the whole-brain simulations do not maintain this molecular specificity, as they require concurrent changes to adaptation parameters that are not directly linked to the pharmacological targets (GABA-A, NMDA) being modeled. This discrepancy between the claimed approach and the actual implementation affects the validity of the conclusions about molecular mechanisms driving whole-brain state changes.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|Claude|2", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "The paper applies uniform synaptic parameter changes across all brain regions when modeling anesthesia, ignoring the well-documented spatial heterogeneity of GABA and NMDA receptor densities across the cortex, which prior whole-brain modeling studies of anesthesia have incorporated.\n\n\"The activity of each region can be described using the developed mean-field model, forming a node in the whole-brain model.\"\nThis description indicates that all 68 brain regions in the model use identical mean-field parameters modified uniformly during anesthesia simulation. There is no mention of region-specific receptor densities or spatially varying parameter changes. This homogeneous approach ignores substantial evidence that GABA-A and NMDA receptor densities vary considerably across cortical regions, which affects how different brain areas respond to anesthetics.\n\n* Quote from Luppi et al. (2022) [[1]](#citation-1): \"By incorporating PET data about the cortical distribution of GABA receptors, our computational model reveals a key role of spatially-specific local inhibition for reproducing the functional MRI activity observed during anaesthesia with the GABA-ergic agent propofol.\"\nLuppi et al. (2022), which this paper cites as prior work, explicitly incorporated PET-derived GABA receptor density maps to achieve spatially heterogeneous inhibition patterns during propofol anesthesia modeling. The current paper does not incorporate any receptor density data despite modeling the same anesthetic (propofol) and claiming methodological advances over prior approaches that \"without explicitly considering the biophysical details of the molecular action.\"\n\"Previous studies have used the mean-field approach to model the macroscopic effects of general anesthesia on the brain at the macroscale (Luppi et al., 2022), and the action of psychedelic compounds on the brain (Deco et al., 2018; Herzog et al., 2023), however, without explicitly considering the biophysical details of the molecular action.\"\nThe paper claims superiority over Luppi et al. (2022) by incorporating \"biophysical details of the molecular action,\" yet Luppi et al. actually used spatially-specific receptor distribution data while the current paper applies uniform parameter changes. This represents a methodological limitation rather than an advancement, as spatially heterogeneous receptor distributions are a biophysically important feature that the current approach neglects.\n\nReferences:\n[1] [Luppi, A.I. et al. (2022). Whole-brain modelling identifies distinct but convergent paths to unconsciousness in anaesthesia and disorders of consciousness. Communications Biology, 5, 384.](https://www.nature.com/articles/s42003-022-03330-y)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|Claude|3", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "The paper presents simulated Perturbational Complexity Index (PCI) values as validation of the model's ability to capture consciousness-related responsiveness, but provides only qualitative visual comparison with empirical data rather than quantitative statistical validation.\n\n\"B. Modified from Casali et al. (2013): Empirical PCI data from human subjects showing a clear distinction between awake and unconscious individuals.\" (Figure 6 caption)\nThe empirical PCI data shown in Figure 6B is borrowed from Casali et al. (2013) but only presented as a separate panel alongside the simulation results. There is no statistical comparison between the simulated PCI values (panel A) and the empirical values (panel B). The simulation and empirical data use different absolute PCI scales (simulation shows values ~0.05-0.3, while the empirical data from the original publication uses different measurement units), making direct comparison impossible without proper normalization or statistical testing.\n\"While PCI values in wake-like condition were significantly higher than the unconscious states (p<0.001), a high degree of overlap was found among the unconscious, with no significant differences detected between the different simulated mechanisms of general anesthesia, although both were lower than NREM sleep.\"\nThe statistical analysis only compares between simulated conditions (wake vs. different unconscious states), not between simulated and empirical data. The lack of significant differences between simulated NMDA-blocker and GABA-A anesthesia conditions (as acknowledged) contrasts with known differential effects of ketamine versus propofol on EEG patterns and consciousness states [[2]](#citation-2), suggesting the model may not capture important distinctions between anesthetic mechanisms.\n\n* Quote from Casali et al. (2013) [[3]](#citation-3): \"A theoretically based index of consciousness independent of sensory processing and behavior.\"\nThe original PCI metric from Casali et al. was validated against extensive empirical TMS-EEG recordings across multiple states (wakefulness, sleep, anesthesia with different agents, disorders of consciousness). The current paper's simulation generates PCI from a square-wave perturbation applied to firing rates, which differs fundamentally from the TMS-evoked EEG responses used in the original metric derivation. This methodological difference is not quantitatively validated, leaving the relationship between simulated and empirical PCI unclear.\n\nReferences:\n[2] [Mashour, G.A. & Hudetz, A.G. (2017). Bottom-up and top-down mechanisms of general anesthetics modulate different dimensions of consciousness. Frontiers in Neural Circuits, 11, 44.](https://www.frontiersin.org/articles/10.3389/fncir.2017.00044/full)\n[3] [Casali, A.G. et al. (2013). A theoretically based index of consciousness independent of sensory processing and behavior. Science Translational Medicine, 5, 198ra105.](https://www.science.org/doi/10.1126/scitranslmed.3006294)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|Claude|4", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "The model's structure-function correlation analysis shows a substantially larger effect size in simulations compared to empirical data, but this discrepancy is neither statistically tested nor adequately discussed.\n\n\"Despite a larger increase of SC-FC correlation in the case of simulated general anesthesia, the model qualitatively reproduced their relative difference.\" (Results section)\nThe paper acknowledges that the simulated effect is larger than the empirical effect but dismisses this as acceptable because the \"qualitative\" pattern is preserved. Looking at Figure 5, the simulated SC-FC correlation increases from approximately 0.30 (awake) to approximately 0.39 (anesthesia), representing a ~30% relative increase. In contrast, the empirical data shows an increase from approximately 0.29 to approximately 0.33, representing only a ~14% relative increase. This ~2-fold difference in effect magnitude is not statistically evaluated, nor is there discussion of what could cause such a discrepancy.\n\"The whole-brain model was used to simulate BOLD signals for the wake-like (\\( b_e = 30\\)pA, \\( \\tau_i = 5\\)ms) and propofol anesthesia (\\( b_e = 30\\)pA, \\( \\tau_i = 7\\)ms) conditions (16 different noise realizations).\"\nThe simulation uses only 16 noise realizations compared to 26 empirical subjects. More importantly, the simulated conditions use \\( b_e = 30\\)pA for both wake and anesthesia states, which is inconsistent with Figure 4 where wakefulness is modeled with \\( b_e = 5\\)pA. This parameter inconsistency across analyses makes it difficult to assess whether the model produces robust, generalizable predictions for SC-FC correlations.\n\"*** p < 0.001 from Mann-Whitney U test.\" (Figure 5 caption)\nWhile the within-group differences (awake vs. anesthesia) are statistically significant for both empirical and simulated data, there is no between-group comparison testing whether the magnitude of change differs significantly between the empirical and simulated datasets. This omission makes it impossible to assess whether the model provides quantitatively accurate predictions or merely reproduces the direction of change with exaggerated magnitude.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|Claude|5", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "While the paper presents parameter scans at the mesoscale level (Figure 3), the whole-brain simulations use only specific parameter combinations without systematic exploration of parameter sensitivity at the macroscale.\n\n\"For each combination of \\( b_e \\) and \\( \\tau_{e,i} \\), 20 different trials with different noise realizations were conducted.\" (Figure 3 caption)\nThe systematic parameter exploration shown in Figure 3 is performed only for mesoscale network simulations. At the whole-brain level, the paper presents results for only a few specific parameter combinations (e.g., wakefulness with \\( b_e = 5\\)pA, anesthesia with \\( b_e = 30\\)pA and altered \\( \\tau \\) values). There is no equivalent systematic exploration of how whole-brain observables (SC-FC correlation, PCI) vary continuously across parameter space, making it difficult to assess the robustness of the reported effects.\n\"The \\( v_{drive} \\) received different values in our simulations depending on the microscopic parameter that was selectively changed.\"\nThe external drive parameter \\( v_{drive} \\) varies across simulations (0.315Hz, 0.345Hz, 0.4Hz, 0.55Hz in different conditions shown in Figure 4) without systematic justification for these specific values. This parameter significantly affects network dynamics, yet its selection appears ad hoc. The lack of sensitivity analysis for \\( v_{drive} \\) at the whole-brain level raises questions about whether the reported state transitions are robust to this parameter choice.\n\"Different seeds (n=16) for noise realizations were implemented to address inter-subject variability.\"\nWhile noise realizations are varied to capture some variability, the core model parameters (\\( b_e \\), \\( \\tau_e \\), \\( \\tau_i \\)) are fixed at specific values for each condition. Without exploring how small perturbations in these parameters affect whole-brain outcomes, it is unclear whether the model predictions are robust or sensitive to precise parameter tuning. This limitation affects the framework's utility for predicting anesthesia effects across individual patients with varying neurobiological parameters.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|GPT|1", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "The paper’s PCI-based validation of “reduced responsiveness” is not reliable because the described 300 ms pre/post-stimulus PCI analysis appears to be mis-implemented in the provided code (time-window indexing mixes milliseconds with time bins and the binarization thresholding is effectively degenerate), directly threatening validity and downstream conclusions tied to Fig. 6.\n\n“60 different trials, each with a different stimulus onset and noise realization, were performed where the analysis concerns an interval of 300 ms pre- and post-stimulus.”\nThis sentence defines the core analysis window used to compute PCI and therefore sets a hard requirement on how the time axis must be indexed in the implementation. If the code indexes a 300 ms window incorrectly (e.g., by treating 300 ms as 300 samples when the simulation time step is not 1 ms), then the computed PCI will not correspond to the stated protocol. Because PCI is sensitive to the spatiotemporal extent and duration of significant activations after perturbation, even a moderate windowing error can change both PCI magnitude and between-condition differences. The rest of the paper treats PCI differences as a validation target (“reduced responsiveness”), so an incorrect window directly undermines that validation. The paper does not provide an independent check (e.g., reproducing canonical PCI behavior on a known dataset) that could catch such implementation errors. Therefore, correctness of the 300 ms window is essential for the validity of the PCI results.\n“The Perturbational Complexity Index (PCI), as proposed by Casali et al. (Casali et al., 2013) is the normalized Lempel-Ziv complexity of the evoked spatiotemporal patterns of cortical activation …”\nThe statement explicitly claims methodological alignment with PCI as introduced in the literature, which raises the bar for faithful implementation details, especially around binarization and time windowing. PCI is defined on “evoked spatiotemporal patterns,” so any change in how the evoked window is extracted or how significant activations are thresholded changes the object whose complexity is measured. When a paper claims it is computing PCI “as proposed,” readers expect that key steps (e.g., time-alignment to stimulus onset and significance thresholding) follow the reference algorithm closely. If the implementation deviates materially, the measured quantity may no longer be comparable to empirical PCI values or to other modeling work. This is particularly important here because PCI is used as a whole-brain validation endpoint tied to consciousness-state claims. A mismatch between claimed and actual PCI computation would therefore threaten both validity and interpretation.\n```python\n# parameter_M_Berlin.py\nself.parameter_integrator={\n    ...\n    'dt': 0.1 # in ms\n}\n\nself.parameter_monitor= {\n    ...\n    'parameter_TemporalAverage':{\n        ...\n        'period':self.parameter_integrator['dt']*10.0\n    },\n}\n```\nThis code shows that the underlying integrator step is 0.1 ms, while downstream monitors can report data at a coarser sampling period (e.g., `dt*10 = 1.0 ms` for the temporal-average monitor). As a result, any analysis that indexes a “300 ms” window must be explicit about whether array indices are in integrator steps, monitor samples, or milliseconds. The PCI code (shown below) mixes a millisecond-valued `t_analysis` with array slicing, which is only correct if the effective sampling is exactly 1 ms and the authors always use a 1 ms monitor for PCI. The manuscript does not specify the monitor sampling used for the evoked-response/PCI computation, so a reader cannot verify that this assumption holds. Because PCI is designed to summarize propagation over hundreds of milliseconds, confusion between units or sampling rates can materially change the computed binary spatiotemporal pattern and its complexity. Therefore, the code’s timebase ambiguity is a substantive validity risk for the PCI results.\n```python\n# functions.py (PCI computation)\n\nt_analysis = 300 #ms\nnbins_analysis =  int(t_analysis/times_l[0])\n...\n\nsig_all_binary = tools.binarise_signals(np.array(sig_cut_analysis), int(t_analysis/times_l[0]),\n                                nshuffles = 10, percentile = 100)\n\nfor ijk in range(n_trials):\n    binJ=sig_all_binary.astype(int)[ijk,:,t_analysis:] # CHECK each row is a time series !\n```\nThe code computes `nbins_analysis = int(t_analysis/times_l[0])`, which correctly converts milliseconds to time bins based on the sampled time step, but then slices using `t_analysis` directly (`t_analysis:`) instead of `nbins_analysis:`. This is only correct when the sampled time step is exactly 1 ms (so that “300 ms” equals 300 bins); otherwise, the window length and alignment will silently change. The manuscript does not document the sampling of the saved evoked time series used for PCI, so the reader cannot verify that the “300 ms” window in Methods is respected. The inline “CHECK” comment suggests that even the authors were uncertain about the intended orientation/indexing of the binary matrix, which is risky for a headline validation metric. Because PCI depends on the temporal extent and ordering of significant activations, a hidden unit mismatch can materially shift PCI distributions across conditions. Therefore, the combination of ambiguous timebase and non-robust indexing makes the PCI results unreliable without clarification and re-analysis.\n```python\n# nuu_tools_simulation_human.py\n\ndef binarise_signals(signal_m, t_stim, nshuffles = 10, percentile = 100):\n    ...\n    max_sorted = np.sort(max_absval_surrogates)\n    signalThresh = max_sorted[-int(nshuffles/percentile)] # correction?\n    ...\n    signal_binary = signalcn > signalThresh\n```\nWith `nshuffles = 10` and `percentile = 100`, `int(nshuffles/percentile)` evaluates to 0, so the index becomes `-0`, which in Python selects the first element (`max_sorted[0]`), i.e., the minimum surrogate maximum. That makes the “significance threshold” extremely permissive, marking many post-stimulus samples as significant even when they would not survive a conventional high-percentile bootstrap threshold. This directly affects the density of 1s in the binary matrix and therefore its source entropy and Lempel–Ziv complexity; both the numerator and denominator of PCI will be distorted by such a threshold. The code itself questions the logic (“# correction?”), which reinforces that this is not a deliberate, well-validated choice. Because the paper’s main PCI conclusion depends on comparing PCI distributions across conditions, a thresholding bug can invert or exaggerate differences. This constitutes a major validity issue for the PCI-based claims.\n“PCI is calculated by (i) perturbing the cortex with transcranial magnetic stimulation (TMS) … and (ii) compressing the spatiotemporal pattern of these electrocortical responses to measure their algorithmic complexity …” [\\[1\\]](#cite1)\nThis description emphasizes that PCI is defined on the spatiotemporal response pattern after perturbation, so the correctness of how that pattern is extracted and binarized is fundamental. If the post-stimulus window is inadvertently shortened, the response pattern being “compressed” is not the one the PCI is meant to measure. Likewise, if the threshold for “significant” activation is set too low, the binary pattern will include widespread activity that is not statistically supported, inflating complexity measures. In both cases, the computed PCI would no longer correspond to the intended operationalization of complexity after perturbation. Since the manuscript uses PCI to argue about consciousness-related responsiveness, miscomputing PCI undermines that argument. Therefore, alignment with the reference definition strengthens the case that the current implementation errors are not minor.\n“During the awake state, TMS elicits rapidly propagating cortical activation … sustaining widespread recurrent activity for approximately 300 ms.” [\\[5\\]](#cite5)\nThis sentence provides an external rationale for why the “hundreds of milliseconds” post-stimulus window matters: the physiological phenomenon PCI is designed to capture unfolds over ~300 ms. If the implementation effectively analyzes a substantially shorter interval (e.g., tens of milliseconds), it will systematically miss late propagation and recurrence, which are key to differentiating conscious vs unconscious responses. This makes the authors’ use of a 300 ms window scientifically meaningful, not arbitrary. It also means a windowing mistake is not just a bookkeeping error but changes the biological interpretation of what is measured. Because the paper claims to reproduce state-dependent propagation differences, analyzing the wrong temporal extent invalidates that comparison. Hence, the code’s ms/bin mismatch directly conflicts with standard expectations about the relevant timescale.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|GPT|2", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "The paper’s “structure–function correlation” result is methodologically fragile because the provided SC–FC coupling computation correlates the flattened full FC and SC matrices (including diagonal and symmetric duplicates), which is not a standard or unbiased estimator of SC–FC coupling and can materially alter the reported effect sizes.\n\n“From these signals, the FC matrix was computed for each participant and correlated with a reference SC. The Pearson correlation between SC and FC was significantly higher during anesthesia compared to wakefulness.”\nThis passage describes a scalar coupling metric (a Pearson correlation between SC and FC) that underpins the paper’s whole-brain validation claim for anesthesia. Because the claim is based on a single summary statistic per subject (and per simulation seed), the exact definition of how SC and FC are vectorized matters substantially. Different common choices—e.g., including/excluding diagonal entries, using only one triangle of symmetric matrices, or applying transformations—change both the value and comparability of the correlation across studies. The manuscript does not specify these details in the Methods beyond “Pearson correlation,” so correctness must be inferred from the code. If the code uses a nonstandard vectorization that inflates correlation (e.g., by including many trivial or duplicated entries), the conclusion about increased SC–FC coupling may be an artifact of the metric rather than a property of the modeled or empirical state. This weakens the reliability of the “mirroring experimental findings” argument.\n```python\ndef corr_sc_fc(BOLD_signal: np.ndarray, TR: float, SC: np.ndarray) -> tuple:\n    signal = preprocess_bold(BOLD_signal, TR, apply_bandpass_YN=False)\n    FC=np.corrcoef(signal.T)\n\n    pearson_FCSC = np.corrcoef(FC.flatten(), SC.flatten()) #this will be a matrix\n    coef = pearson_FCSC[0, 1]\n\n    return FC, coef\n```\nThis implementation correlates `FC.flatten()` with `SC.flatten()`, which includes diagonal entries and both upper and lower triangles of each symmetric matrix. Including diagonal/self-correlation terms (which are typically 1 in FC and often 0/undefined in SC, depending on convention) can dominate the statistic and bias the correlation. Including both triangles also duplicates each undirected edge twice, effectively re-weighting edges and inflating apparent sample size without adding information; this can change the computed correlation and its variance. Standard SC–FC coupling analyses typically vectorize a single triangle and often discard the diagonal specifically to avoid these issues. Because the paper’s effect is an increase in correlation, any systematic inflation from duplicated/diagonal terms can artificially enlarge the reported difference. As a result, the method as coded does not provide a robust basis for the claimed structure–function coupling changes.\n“Return the flattened lower triangular part of an array.” and “If True, the values of the diagonal are not returned.” [\\[3\\]](#cite3)\nThis documentation reflects a common, well-established practice in connectomics tooling: symmetric connectivity matrices are converted to vectors by taking only one triangle, optionally excluding the diagonal. The reason is precisely to avoid double-counting symmetric entries and to control the role of the diagonal, which otherwise introduces trivial or non-comparable values. When authors claim a Pearson correlation between FC and SC, most readers in the field will assume such a triangular vectorization, because it matches how FC/SC are typically treated as edge lists. The paper’s current implementation instead uses the full flattening, which deviates from this established convention. This makes it hard to compare the reported SC–FC correlations to prior literature and raises concern that the quantitative magnitude (and possibly direction) of effects depends on a nonstandard implementation choice. Therefore, the Nilearn documentation provides direct external evidence that the paper’s chosen vectorization is not the expected one.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|GPT|3", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "The statistical testing for the empirical and simulated SC–FC coupling difference is not appropriate because the manuscript reports a Mann–Whitney U test even though the design implies paired measurements (same participants in both states; and seeds can be paired across conditions), making p-values and significance claims unreliable.\n\n“Resting-state fMRI data from 26 individuals during wakefulness and under propofol anesthesia were analysed.”\nThis sentence strongly implies a within-subject (paired) design: the same 26 individuals contribute data in two conditions (wakefulness and propofol). In paired designs, subject-specific baseline differences are controlled by comparing within-subject changes, and independence assumptions between the two condition samples do not hold. Treating the two condition samples as independent can change both the test statistic and p-value, and it typically reduces power or yields misleading inference depending on correlation structure. Because the “significantly higher” claim is a key validation point for the model, using the wrong test threatens the reliability of a central result. The paper does not justify why a paired test was not used or whether the samples were actually independent, leaving the reader unable to trust the reported significance. Thus, the study design described in the manuscript conflicts with the reported statistical test.\n“*** p < 0.001 from Mann-Whitney U test.”\nThis figure-caption claim asserts strong statistical significance using a specific test, so correctness of the test’s assumptions is essential. The Mann–Whitney U test is designed for two independent samples, not repeated measurements from the same participants. Using it on paired data effectively ignores within-subject pairing, which is standard practice in anesthesia datasets where both awake and anesthetized scans are collected from the same participants. Moreover, the caption also applies the same test to simulated “noise realizations,” which can be paired by seed when the analysis already plots wake/unconscious pairs on the same axis in Fig. 6. If pairing exists but is ignored, the p-value does not correspond to the intended null hypothesis about condition effects within subjects/seeds. Because the claim is presented as a key quantitative validation, this mis-specification undermines the paper’s conclusions.\n“Perform the Mann-Whitney U rank test on two independent samples.” and “mannwhitneyu is for independent samples. For related / paired samples, consider scipy.stats.wilcoxon.” [\\[2\\]](#cite2)\nThis reference explicitly states the independence requirement of the Mann–Whitney U test and points to a paired alternative (Wilcoxon signed-rank) for related samples. Given the manuscript’s phrasing about the same individuals under two conditions, a paired test is the standard and expected choice. The SciPy documentation is a clear, authoritative statement of the statistical assumption, making it straightforward to evaluate whether the manuscript’s test choice matches the design. Because the authors report a very small p-value, readers may over-trust the strength of evidence unless the test is correctly matched to the sampling scheme. This mismatch is not a minor reporting issue: it can change inference and the interpretation of whether the effect is robust across individuals. Hence, the external documentation supports that the manuscript’s reported test is inappropriate for the implied data structure.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|GPT|4", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "The paper’s empirical SC–FC validation is not reproducible as described because the manuscript claims a 68-region Desikan–Killiany parcellation and a specific reference SC, but the provided “data availability” link points to a dataset of 400-ROI FC matrices (Schaefer parcellation) without the structural connectivity used, leaving an unclear mapping between shared data and the paper’s reported analysis.\n\n“We employed a parcellation scheme of a human brain comprising 68 brain regions (Anatomical Desikan-Killiany Atlas (Desikan et al., 2006)) …”\nThis sentence specifies a concrete parcellation choice that determines the dimensionality of both FC and SC in the SC–FC coupling analysis (68×68). Parcellation choice is not a cosmetic detail: SC–FC correlations depend on atlas resolution and the mapping between time series, FC, and SC. Therefore, any shared data intended to reproduce the analysis should correspond to (or be mappable into) this 68-region atlas. If the shared data uses a different atlas with a different number of regions, reproducing the exact SC–FC correlations in the paper requires additional, nontrivial processing steps (e.g., re-parcellation or aggregation) that must be specified. The manuscript does not provide such a mapping procedure. Hence, the parcellation statement creates a concrete reproducibility requirement that must match the shared data.\n“Data used in this article can be found in https://zenodo.org/records/6955280”\nThis is the paper’s explicit claim about where readers can obtain the data needed to reproduce results. Because the paper uses empirical SC–FC results as a validation target, the linked record should contain enough information to reconstruct the FC matrices, the reference SC, and the correlation analysis. If it does not, then the “data used in this article” statement is misleading with respect to reproducibility. The paper does not qualify which parts of the article are reproducible from that link (e.g., only FC but not SC), nor does it provide a second link for the missing elements. For a core validation figure, this level of ambiguity is a substantial obstacle to independent verification. Thus, this sentence is central to the reproducibility concern.\n“Following fMRI data preprocessing, the fMRI time courses were extracted from 400 cortical areas … (Schaefer's 400 ROIs). A connectivity matrix was then calculated … resulting in a 400x400 connectivity matrix for each participant and each condition.” [\\[4\\]](#cite4)\nThe Zenodo record linked by the paper documents FC matrices at a different resolution (400×400) and a different parcellation than the 68-region Desikan–Killiany atlas claimed in the manuscript. Without an explicit aggregation or mapping strategy, a reader cannot reproduce a 68×68 SC–FC correlation from 400×400 FC matrices in a principled way. Moreover, the record description indicates it provides functional connectivity matrices, but it does not indicate that it includes the structural connectivity matrix (“reference SC”) used in the manuscript’s SC–FC correlation. Because the manuscript’s SC–FC metric requires both FC and SC in the same parcellation, the provided data link is insufficient to reproduce the stated analysis as written. This mismatch is significant because it blocks replication of one of the paper’s key empirical validations. Therefore, the Zenodo description directly evidences a reproducibility gap.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "The paper claims to model the effects of propofol anesthesia but fails to reproduce the characteristic frontal alpha oscillations (8-12 Hz) that are a hallmark of propofol-induced unconsciousness, instead producing only generalized slow-wave activity similar to sleep.\n\n\"We show that anesthetics targeting GABA_A and NMDA receptors can switch brain activity to generalized slow-wave patterns, as observed experimentally in deep anesthesia.\"\nThe authors state that their model produces \"generalized slow-wave patterns\". While slow waves are present in deep anesthesia, the specific signature of propofol at surgical levels (where loss of consciousness occurs) is the \"alpha-slow wave\" complex, particularly the anteriorization of alpha power. By only reproducing slow waves, the model fails to distinguish propofol anesthesia from NREM sleep or other coma states, missing a critical physiological feature of the drug it claims to model.\n\"This type of activity is also found in NREM sleep... where the low levels of acetylcholine lead to the activation of leak K+ channels... Variations in the level of acetylcholine are also observed for anesthetics such as propofol\"\nThe authors draw a parallel between their simulated anesthesia state and NREM sleep. However, experimentally, propofol anesthesia is distinct from NREM sleep precisely due to the presence of coherent alpha oscillations, which are not prominent in NREM sleep (which is characterized by spindles and slow waves). The model's inability to capture this distinction suggests it may be oversimplified.\n\"Electroencephalogram signatures of loss and recovery of consciousness from propofol\" [1]\nThis seminal paper by Purdon et al. (2013) clearly establishes that propofol-induced unconsciousness is characterized by a strong increase in alpha (8-12 Hz) power, often coupled with slow waves. A biophysically grounded model of propofol should ideally be able to reproduce this spectral signature, or at least discuss why it is absent.\n\nReferences:\n[1] Purdon, P. L., et al. (2013). Electroencephalogram signatures of loss and recovery of consciousness from propofol. Proceedings of the National Academy of Sciences, 110(12), E1142-E1151. https://doi.org/10.1073/pnas.1221180110", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "The authors use a Transfer Function (TF) fitted for baseline neuronal parameters to simulate anesthesia conditions involving large changes in synaptic time constants, without validating that the mean-field approximation holds in this new regime.\n\n\"As shown in Di Volo et al. (2019) [4] the mean-field predictions work even far from the fitting point of the TF, so in all the examples showcased in this work we used previously calculated P, fitted for similar parameterizations of the two types of cells\"\nThe authors explicitly state they use pre-calculated polynomial coefficients ($P$) for the transfer function. These coefficients are fitted to map the subthreshold statistics ($\\mu_V, \\sigma_V, \\tau_V$) to the firing rate. However, the \"phenomenological threshold\" approximation relies on the assumption that the noise properties (colored noise) are adequately captured by $\\tau_V$. Anesthesia involves drastic changes in synaptic decay times (e.g., $\\tau_i$ increasing by 3-5 fold for propofol), which significantly alters the spectral content of the synaptic noise. It is not guaranteed that the TF fitted for baseline $\\tau$ values remains accurate for such large deviations.\n\"Thus, the main effect of these anesthetics on cortical synapses can be described as an increase in the time constant of inhibitory synaptic decay... while a decrease in the excitatory synaptic decay time\"\nThe core of the paper's methodology is modifying these time constants. Without showing a direct comparison between the Spiking Neural Network (SNN) firing rates and the Mean-Field predictions *specifically* for the anesthesia parameters (large $\\tau_i$, small $\\tau_e$), the validity of the mean-field model in this regime is unproven. The paper relies on the general robustness claimed by previous work rather than demonstrating it for the specific application at hand.\n\nReferences:\n[4] Di Volo, M., et al. (2019). Biologically realistic mean-field models of conductance-based networks of spiking neurons with adaptation. Neural Computation, 31(4), 653-680. https://doi.org/10.1162/neco_a_01173", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "The model characterizes the effect of propofol solely as an increase in the inhibitory synaptic decay time constant, neglecting the drug's significant effect on tonic inhibition (extrasynaptic GABA_A receptors) and leak currents.\n\n\"Thus, the main effect of these anesthetics on cortical synapses can be described as an increase in the time constant of inhibitory synaptic decay (\\( \\tau_i \\) in Eq. 4) to account for the IPSP prolongation caused by GABAergic anesthetics\"\nWhile propofol does prolong IPSPs, it also potently enhances tonic inhibition mediated by extrasynaptic GABA_A receptors, which leads to a persistent hyperpolarizing current and increased membrane conductance (leak). This effect is crucial for silencing neurons and contributing to the \"down\" states of the slow oscillation. By modeling only the synaptic decay ($\\tau_i$), the authors ignore a fundamental mechanism that alters the resting membrane potential and excitability of the neurons.\n\"General anesthetics and molecular mechanisms of unconsciousness\" [2]\nThis review (cited in the paper as Forman SA, 2008) and others in the field acknowledge that general anesthetics affect multiple targets. For propofol, the enhancement of tonic current is a major factor in reducing neuronal excitability, distinct from the prolongation of phasic synaptic events. Neglecting this leads to an incomplete biophysical description.\n\nReferences:\n[2] Forman, S. A., & Chin, V. A. (2008). General anesthetics and molecular mechanisms of unconsciousness. International anesthesiology clinics, 46(3), 43. https://doi.org/10.1097/AIA.0b013e3181755da5", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "The validation of the whole-brain model is primarily qualitative (observing slow waves and reduced responsiveness) and lacks a rigorous quantitative comparison with experimental neuroimaging data.\n\n\"To yield more precise models providing a quantitative comparison with experimental data, it is crucial to accurately reconstruct brain signals (such as EEG, MEG or MRI) from mean-field models... which will allow a more direct comparison with experiments.\"\nThe authors acknowledge this limitation in the Discussion, admitting that they have not yet achieved a \"quantitative comparison\". However, for a paper titled \"A computational approach to evaluate...\", the lack of quantitative validation (e.g., comparing the power spectrum of simulated signals with real anesthesia EEG, or comparing the functional connectivity matrices using a distance metric) weakens the conclusions. The \"evaluation\" remains largely theoretical and qualitative.\n\"We show that anesthetics targeting GABA_A and NMDA receptors can switch brain activity to generalized slow-wave patterns, as observed experimentally in deep anesthesia.\"\nThis claim is based on the visual similarity of the dynamics (slow waves) rather than a statistical comparison. Many different models can produce slow waves. A quantitative metric (like the Kullback-Leibler divergence between simulated and empirical spectra) would be necessary to claim the model \"successfully captures\" the transition.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "The propagation of the NMDA and GABA receptor properties from the spiking network to the mean field model to the virtual brain model is not explained. For example, the mean field model does not show any parameters directly related to NMDA or GABA receptors. The parameters of the mean filed model that are closest to NMDA and GABA receptor currents, Tau-e and Tau-I, do not appear in any of the equations reported in the Methods. This explanation is crucial but is missing. An explanation here is needed, also for the sake of reproducibility.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "The paper is about the propagation of molecular-level properties to higher scales, but I the ntro the impact of pharmaceutical compounds is declared. The pharmacological issue here is a reflection of the simulation of changes in membrane receptor functions. There is no specific workflow to simulate drugs acting on the receptors though. This should be clarified.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "The authors simulate state transition of cortical activity from wakefulness to sleep. The change is evident in the spiking network, in the mean field model, and in the virtual brain model. This is a nice in silico experiment. However, the discussion of results shown in Fig. 5 and 6 is very limited.\\n\\n- What about the firing rate of the E and I neurons ? By the way, in the mean filed model two neurons represent more than 50 types of neurons of a cortical column that contains more than 30000 neurons as a whole. This should be explained. Any comparison between mean field model firgin rates and those of the spiking network when anesthesia states are simulated ?\\n\\n- Fig. 6 looks quite rich of information, but it is not described or commented beyond the figure legend. It must be described in order to make it understandable.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "How are the single cell model parameters related to the mean field model parameter? In other words, how were the effects at the microscale incorporated in the macroscale model. For example, is the mean field time constant T related in some functional way to the 'taus that were manipulated to simulate effects of anesthetics. A description of this would be useful as this is the most salient feature of this paper.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "This is a forward model and produces output data that matches with experimental data. It would be useful for the reader to have a discussion on how one could use this framework to systematically estimate model parameters such as the 'taus if one has the experimental data. For example, if we had the EEG/MEG recordings, can we use this data to find what model parameters are necessary to produce this observed brain recording. This would be in my opinion crucial for designing therapeutics and would take this approach one step closer to translation.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "The paper investigates the structure-function relationship in reference and anaesthesia cases. However, it does not reveal how well the model can capture whole-brain dynamics in terms of Functional connectivity, a traditional benchmark for the prediction power of the model. The authors can refer to the work of Luppi et al. (https://www.nature.com/articles/s42003-022-03330-y), where the model was tested with the Functional connectivity dynamics (FCD). A similar analysis can investigate the precision of the model.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "The paper could better define the spiking network. It would be beneficial to include a description in the methods section regarding how the network was constructed and the rationale behind using 80% pyramidal (excitatory) neurons and 20% interneurons (inhibitory). A reference may suffice in this instance.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "The model investigates the underlying dynamics of the model by analyzing the excitatory firing pattern with the transfer function associated with it, and the transition state was shown with the loss of a stable self-sustained state and the emergence of an up-down state. However, it’s difficult to follow this in section 2.6. “Emergence of UP and Down states……” a basic description is needed to make the paper self-sufficient. Some of the arguments from the earlier work by Di Volo et al. (2019) can be added to clarify the rationale behind referring to it as an ‘Up and Down’ state and the bistable behaviour of the model. As it is one of the central arguments of the work reflecting the impact of the parameters describing the interventions of propofol, it should be stated clearly.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "The frequent references to the NREM sleep stage make the results section somewhat confusing. The comparison and analysis should either be discussed separately or mentioned in the discussion section. It is challenging to distinguish outcomes pertaining to anaesthesia cases from those related to sleep stages.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "In the figures given in Fig. 6 A and B, it is impossible to follow the scattered plots for PCI (Perturbational Complexity Index) and make inferences from them. The authors can remove it by replacing it with a simple box plot with statistical analysis, which is enough to showcase the difference.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "In the Discussion, the paper lacks the proper comparative analysis. A brief discussion about the superiority of the model over the existing ones (i.e. Luppi et al., Deco et al. (2018), referenced in the paper but not discussed) can be described in terms of what can be inferred from the model, which is not possible from the other models. These arguments will make a strong case for this modelling approach.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|Human_3|7", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "The paper needs a parameter table to track the changes in parameters at a glance for different cases. Some of the parameters are not even available, like- Vc in the equation in line number 684. It looks like it is a velocity parameter that incorporates the delay information. However, its importance has been shown in earlier mean filed models like- Castaldo et al. (2023) https://doi.org/10.1016/j.neuroimage.2023.120236.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|Human_3|8", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "The provided code is not annotated fully. It’s difficult to follow it seamlessly and produce the results given in the paper. Authors can add a parameter file or clearly mention the parameters involved in the paper to produce the results.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|Human_3|9", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "In the summary of Figure 4, the authors mention UD. What is it?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|Human_3|10", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "In line 408, the authors talked about correlating SC with FC. The term “Reference SC” is used. Please clarify it. Is it a mean SC of all the individuals or an individual SC? Is the model a personalized model meaning a separate SC used to compute the FC of each person?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|Human_3|11", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "The chronology of numbering for the equations is not followed; some are numbered, and some are not. Please enumerate them.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|23|Human_3|12", "source": "prb", "split": "test", "paper_id": "prb23", "comment": "In line 743, the phrase “significant vectors…” sounds vague. Rephrase it.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Claude|1", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "The paper makes speculative causal claims about visual memory consolidation based solely on electrophysiological findings without any behavioral or cognitive measures to support this interpretation.\n\n\"Our study suggests that phase-amplitude coupling between physiologic HFO and delta waves, as rated by MI, is strengthened during development, in the occipital lobe particularly during toddlerhood and preschool. Given that occipital delta-nested HFO are believed to support visual memory consolidation, our observations imply that process may be significantly strengthened during early childhood.\"\nThis statement presents a causal inference that links electrophysiological measurements (MI in the occipital lobe) to a cognitive process (visual memory consolidation) without any behavioral evidence. The study did not measure visual memory performance at any age, nor did it correlate MI values with any cognitive outcome. The logical leap from \"MI increases with age in occipital lobe\" to \"visual memory consolidation is strengthened\" requires direct behavioral validation that is absent from this study.\n\"one possible explanation for the developmental enhancement of occipital MI is that the cerebral cortex learns to generate HFO at a preferred phase of background rhythms in an experience-dependent manner, optimizing visual memory consolidation during slow-wave sleep (Ji and Wilson, 2007; Mehta, 2007; Sasaki et al., 2010; Buzsáki and da Silva, 2012; Nagasawa et al., 2012).\"\nThe cited studies (particularly Ji and Wilson, 2007) were conducted in rodents using place cells in the hippocampus and visual cortex. The translation of these findings to human developmental changes in phase-amplitude coupling is speculative. Prior research on sleep-dependent memory consolidation in humans has emphasized the need for direct electrophysiology-behavior correlations, particularly in human intracranial studies where such correlations can be directly tested ([1]). The absence of any behavioral measures in this study undermines the validity of claims about memory consolidation.\n\n* Quote from literature: \"Beyond general suppression, sleep and its disruption appear to influence AHN differentially along the dorsoventral hippocampal axis. While studies in rodents have shown that sleep deprivation preferentially impairs neurogenesis in the ventral DG... it has also been reported that REM sleep deprivation can also reduce cell proliferation in the dorsal DG and impair hippocampal-dependent spatial memory.\" ([2])\nThe literature demonstrates that linking electrophysiological markers to memory consolidation requires behavioral validation, as the relationship between neural oscillations and memory function is complex and species-specific. The paper's claims about visual memory consolidation in human children based on occipital MI measurements alone represent an overinterpretation without the necessary behavioral evidence.\n\nReferences:\n[1] [Electrophysiological markers of memory consolidation in the human hippocampus](https://www.pnas.org/doi/10.1073/pnas.2123430119) - Paller et al. PNAS 2022\n[2] [Modifying Factors of Adult Hippocampal Neurogenesis](https://www.mdpi.com/2073-4409/15/1/59) - Cells 2024", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Claude|2", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "The paper's emphasis on early childhood (ages 1-3.9 years) as a critical period for developmental changes in MI is undermined by analyzing only 14 patients in this age group, which provides insufficient statistical power for robust normative atlas construction.\n\n\"The mixed model analysis of iEEG data of 14 children aged from 1.0 and 3.9 suggested that, as compared to the other lobes, the occipital lobe showed higher MI ≥80 Hz & 0.5-1 Hz (mixed model effect: +0.087 [95%CI: +0.078 to +0.097]; uncorrected p-value: < 0.001)\"\nWhile the p-value is significant, the analysis is based on only 14 children across a 3-year developmental window. Given the rapid neurodevelopmental changes during this period and the study's goal of creating a \"normative atlas,\" this sample size is insufficient to establish reliable developmental norms. The paper's hypothesis specifically highlights early childhood as a critical period (\"pattern recognition memory is known to improve most rapidly before six years of age\"), yet the data from this period is the least robust.\n\"In a previous study, we created normative atlases of MI and HFO based on data from 47 patients aged between 4 and 19 years, which revealed a general enhancement of these measures in the occipital lobe (Kuroda et al., 2021). In the current study, we aimed to replicate this finding in a cohort of 14 children aged between 1.0 and 3.9 years and 100 individuals aged 4 years or older.\"\nThe asymmetry between the sample sizes (14 children vs. 100 older individuals) creates an imbalance that makes developmental comparisons across age groups problematic. The claims about developmental trajectories being \"drastic during young childhood\" (as indicated by AIC comparisons of model fits) rely heavily on data from this small subsample, undermining the reliability of these conclusions.\n\n* Quote from literature: \"The most important limitation of this study is the small sample size of children, which also results in reduced statistical power. We did not apply corrections for multiple comparisons because of the exploratory nature of the analysis.\" ([3])\nThis limitation from other neuroimaging studies highlights a recognized problem in the field: small pediatric samples lead to reduced statistical power and unreliable developmental inferences. For a study aiming to create \"normative atlases\" that will serve as clinical references, the sample of 14 young children (spanning 3 years of development) is inadequate to establish reliable age-specific norms.\n\nReferences:\n[3] [Cross-sectional study EEG connectivity patterns in children](https://www.nature.com/articles/s41598-025-33555-w_reference.pdf) - Scientific Reports 2025", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Claude|3", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "The tractography analysis uses an adult-derived population-averaged DWI atlas from healthy adults to infer white matter connectivity in children as young as 1 year old, which is inappropriate given the substantial differences in white matter structure between children and adults.\n\n\"We delineated white matter DWI streamlines using open-source data from 1,065 healthy participants (http://brain.labsolver.org/diffusion-mri-templates/hcp-842-hcp-1021; Yeh et al., 2018)\"\nThe HCP dataset consists of young adults (ages 22-35), not children. Using this atlas to trace white matter pathways supposedly connecting cortical regions showing developmental changes in MI in children aged 1-20 years introduces systematic bias. Pediatric white matter differs substantially from adult white matter in terms of myelination, tract volume, and connectivity patterns, particularly in children under 5 years old.\n\"Our group validated the use of open-source DWI data by demonstrating that the inferred velocity of neural propagations induced by single-pulse electrical stimulation was similar whether using open-source or individual patient DWI data (Sonoda et al., 2021).\"\nThis validation refers to neural propagation velocity, not anatomical accuracy of tract identification in children. The validation does not address whether adult-derived tractography templates accurately represent the anatomical connectivity patterns in developing brains, which is the critical question for interpreting developmental co-growth patterns.\n\n* Quote from literature: \"There have been existing atlases created based on specific populations. But they often struggle to generalize across different age groups... A future direction will be to extend the atlas to include high-quality lifespan datasets, covering a broader range of age groups, and thus enabling the investigation of WM development across the full lifespan.\" ([4])\nRecent literature explicitly acknowledges that population-averaged tractography atlases struggle to generalize across age groups and that age-specific or lifespan atlases are needed for developmental research. The paper's use of an adult atlas to interpret findings in patients as young as 1 year old represents a methodological mismatch that undermines the validity of the tractography-based developmental interpretations shown in Figure 5.\n\nReferences:\n[4] [Cross-Population White Matter Atlas Creation for Neonatal-Adult Brain Comparison](https://arxiv.org/html/2512.20370) - arXiv 2024", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Claude|4", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "The finding that HFO rate is elevated in the occipital lobe shows substantial inconsistency across the four different HFO detection methods, particularly in young children, which undermines the robustness and generalizability of the conclusions.\n\n\"The mixed-model analysis of iEEG data from 14 children between the ages of 1.0 and 3.9 did not show a higher HFO rate in the occipital lobe compared to extra-occipital lobes, except when considering the HFO rate defined by the Hilbert method (HFO STE ≥80 Hz mixed model effect: +0.022 [95%CI: -0.039 to +0.082]; uncorrected p-value: 0.48; HFO SLL ≥80 Hz mixed model effect: +0.036 [95%CI: -0.46 to +0.53]; uncorrected p-value: 0.89; HFO HIL ≥80 Hz mixed model effect: +0.84 [95%CI: +0.57 to +1.1]; uncorrected p-value: < 0.001; HFO MNI ≥80 Hz mixed model effect: -0.044 [95%CI: -0.90 to +3.0 x 10⁻³]; uncorrected p-value: 0.067).\"\nIn young children, three out of four detection methods (STE, SLL, MNI) fail to show significant occipital enhancement of HFO, while only the Hilbert method shows significance. This inconsistency raises concerns about whether the reported occipital HFO enhancement is a robust biological phenomenon or an artifact of specific detection algorithms. For findings intended to serve as normative references for clinical applications, such method-dependent variability is problematic.\n\"Another mixed-model analysis of iEEG data from 100 individuals between the ages of 4.0 and 41.5 demonstrated that the occipital lobe had a higher HFO rate compared to the extra-occipital lobes, except when considering the HFO rate defined by the MNI method (HFO STE ≥80 Hz mixed model effect: +0.14... HFO MNI ≥80 Hz mixed model effect: +0.043 [95%CI: -0.014 to +0.099]; uncorrected p-value: 0.14).\"\nEven in the larger sample of older patients, the MNI method consistently fails to detect occipital HFO enhancement. The paper attempts to explain this as a methodological feature (\"its detector being designed to be agnostic to persistent forms of high-frequency activity\"), but this explanation highlights that different HFO definitions yield different biological conclusions. This undermines the paper's claim to provide generalizable normative data.\n\n* Quote from literature: \"HFOs in iEEG recordings have emerged as promising clinical biomarkers for identifying epileptogenic brain regions. Characterized by brief, synchronized transients in the 80–500 Hz range, their detection has improved through... Universal automated high frequency oscillation detector for real-time, long term eeg.\" ([5])\nThe literature demonstrates ongoing efforts to standardize HFO detection precisely because different methods yield different results. The substantial method-dependent variability in this paper's findings (particularly the complete failure of MNI method to detect developmental patterns that other methods detect) suggests that the normative atlas may not be robust enough for clinical implementation without specifying which detection method should be used.\n\nReferences:\n[5] [Adaptive neuromodulation dialogues - High-frequency oscillations as biomarkers](https://pmc.ncbi.nlm.nih.gov/articles/PMC12715846/) - PMC 2024", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Claude|5", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "The study uses number of antiseizure medications as a proxy for seizure-related cognitive burden in statistical models, but does not adequately account for direct pharmacological effects of these medications on the measured electrophysiological biomarkers (MI and HFO rate).\n\n\"We considered a larger number of antiseizure medications as a surrogate of a more severe seizure-related cognitive burden since polytherapy is associated with more disabling seizures and seizure-related cognitive impairment (Kwan and Brodie, 2001; Kuroda et al., 2021). We employed this approach since no single neuropsychological assessment can quantify the severity of cognitive impairment across all age ranges.\"\nThis approach conflates two distinct effects: (1) seizure-related cognitive burden and (2) direct medication effects on EEG activity. Antiseizure medications are known to directly affect EEG oscillatory activity, including high-frequency components. By treating medication count as a proxy for cognitive burden rather than as a potential direct confounder of the electrophysiological measures, the study may underestimate or misattribute medication effects on MI and HFO.\n\"we employed mixed model analysis to control the effects of potential confounding factors on MI/HFO measures, including antiseizure medications, presence of MRI-visible lesions, and locations of SOZ.\"\nThe mixed model includes medication count as a covariate, but does not account for specific medication types, doses, or their known differential effects on neuronal oscillations. Different antiseizure medications have distinct mechanisms of action (sodium channel blockers, GABA enhancers, etc.) that differentially affect high-frequency activity. The analysis treats all medications as equivalent units, which may not adequately control for pharmacological confounding.\n\n* Quote from literature: \"In new onset epilepsy (NOE), antiseizure medication (ASM) is the first-line treatment... A recent study investigated global connectivity and regional connectivity to assess the impact of antiepileptic drug (AED) administered in patients with temporal lobe.\" ([6])\nRecent literature explicitly examines how antiseizure medications affect EEG connectivity patterns, demonstrating that medication effects are a recognized confounder in iEEG studies. The failure to address specific medication effects (beyond simple count) represents a methodological limitation that could affect the interpretation of developmental changes in MI and HFO, particularly given that younger patients in the sample may have different medication profiles than older patients.\n\nReferences:\n[6] [Linking New Onset Epilepsy Risk-of-Relapse to EEG Patterns](https://journals.lww.com/clinicalneurophys/fulltext/9900/linking_new_onset_epilepsy_risk_of_relapse_to_eeg.287.aspx) - Journal of Clinical Neurophysiology 2024", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|GPT|1", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "This paper’s whole-cortex developmental atlases rely on mesh-point-wise univariate regressions whose inferential procedure appears to under-correct for the thousands of simultaneous mesh-point tests, undermining the validity of the reported “significant” developmental effects (Validity; Appropriate use of statistics and treatment of uncertainties; Conclusions).\n\n\"We identified the mesh points where the developmental change (enhancement or diminution) of a given iEEG biomarker measure survived an FDR correction (for 18 comparisons: six iEEG measures × three types of age measures) in the resulting normative atlas.\"\nThis sentence defines the multiple-comparisons correction scope as 18 comparisons, which accounts for biomarker/age-transform choices but not for the much larger number of mesh points tested across the cortical surface. Because each mesh point is itself a separate hypothesis test, controlling error rates over only 18 comparisons does not control the overall false positive rate of the atlas. In surface/voxel-wise mapping, the dominant multiplicity problem is typically the number of spatial tests (often thousands to hundreds of thousands), not just the number of model variants. As written, the procedure can label mesh points as “significant” even if the family-wise error across the surface is uncontrolled. This directly threatens the reliability of the spatial patterns that the atlas visualizes and the downstream analyses built on those “significant” points.\n\"Univariate regression models, incorporating √age as an independent variable, found that 159 out of the 9464 cortical mesh points (1.7%) showed significantly positive regression slopes, whereas no cortical mesh points showed significantly negative regression slopes.\"\nThis sentence confirms that thousands of mesh-point tests (9,464) were conducted and then thresholded into “significant” vs. non-significant sets. When so many spatial hypotheses are tested, the correction method must explicitly control error rates over those 9,464 tests (or use a spatially-aware alternative such as permutation/cluster-wise inference). Reporting a fraction of significant points without clarifying a surface-wide correction invites the possibility that many detected points are driven by chance, spatial autocorrelation, or model mis-specification. The fact that significance is summarized at the mesh-point level also implies that the atlas’ key claims (where development “occurs”) depend on this thresholding step. If the correction scope is inadequate, the reported 159 “significant” points may not be reproducible under standard whole-brain multiple-testing control. This is a major validity concern because the tractography analysis later conditions on these significant mesh points.\n\"With at least one test performed for every voxel in an image, some correction of the thresholds is needed to control the error rates\" ([1](https://pubmed.ncbi.nlm.nih.gov/11906227/)).\nThis statement captures the standard neuroimaging multiple-testing problem that also applies to cortical-surface mesh-point testing: many spatial locations each contribute at least one statistical test. The paper under review explicitly runs mesh-point-level regressions across 9,464 mesh points, which is directly analogous to voxel-wise testing. Therefore, the correction should address the multiplicity induced by the number of mesh points (the spatial tests), not merely the number of biomarker/age-model variants. Citing an FDR correction over 18 comparisons does not meet the “one test per voxel/mesh point” correction principle described here. As a result, the atlas’ displayed “significant developmental change” regions may be overstated. This mismatch between established neuroimaging practice and the paper’s stated correction scope undermines confidence in the reported atlas-level inferences.\n\"Permutation methods can provide exact control of false positives\" ([2](https://pubmed.ncbi.nlm.nih.gov/24530839/)).\nThis sentence illustrates a common and widely accepted alternative for controlling false positives in mass-univariate imaging analyses, especially when assumptions are weak or complex dependence structures exist. In the paper under review, mesh-point-wise regressions are performed across many spatial tests on data that are not naturally independent (multiple electrodes per patient and spatial smoothing/interpolation). In such contexts, permutation-based family-wise error control or other mass-univariate correction strategies are standard tools to ensure valid inference. The quote highlights that robust false-positive control is achievable and expected in typical imaging scenarios. Because the paper does not describe a surface-wide permutation/cluster correction (and instead describes an 18-comparison FDR), it is unclear that it achieves the level of false-positive control suggested here. This further supports the concern that the reported significant mesh-point findings may be inflated.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|GPT|2", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "The paper’s “dynamic tractography” interpretation (white-matter pathways supporting developmental MI co-growth) is not well supported because it uses population-averaged open-source diffusion tractography (rather than age-matched or subject-specific diffusion data) and conditions connectivity on the paper’s thresholded mesh-point significance results (Validity; Conclusions; Data and methodology).\n\n\"We delineated white matter DWI streamlines using open-source data from 1,065 healthy participants (http://brain.labsolver.org/diffusion-mri-templates/hcp-842-hcp-1021; Yeh et al., 2018), as previously reported (Mitsuhashi et al., 2021, 2022; Sonoda et al., 2021; Kitazawa et al., 2023; Ono et al., 2023).\"\nThis sentence shows that the tractography is not derived from the study’s own cohort, but from an external, population-averaged diffusion template. That choice can be useful for coarse anatomical illustration, but it weakens claims about developmental white-matter connectivity because the diffusion pathways are not estimated in the same individuals (or ages) from whom MI developmental slopes are measured. The approach also implicitly assumes that tract geometry/connectivity is sufficiently invariant across development to justify using a single template, yet the paper’s narrative frames the tractography as reflecting developmental neural communications. Moreover, because the diffusion data are external and averaged, subject-specific variability and age-related changes in tract properties (which are central to a developmental claim) are not represented. As a result, the tractography component is at risk of being an anatomical overlay rather than evidence for developmentally changing pathways linked to MI.\n\"We interpret the visualized streamlines, including vertical occipital fasciculi and posterior callosal fibers, to reflect the ongoing development of large-scale neural communications based on slow wave-nested HFO before reaching the adult level.\"\nThis sentence makes a strong developmental and mechanistic interpretation of the tractography visualization. However, the tractography is not measured longitudinally in the same participants and (as stated in Methods) is drawn from an open-source diffusion template rather than pediatric diffusion data aligned to each age. Consequently, the visualization can at best show that significant cortical regions (as defined by the paper’s statistical thresholding) are anatomically connected by known tracts in a template, not that those tracts are developing in tandem with MI changes. The leap from “connected in a template” to “reflect ongoing development of neural communications” is therefore not warranted by the presented methodology. This over-interpretation materially affects the Conclusions because it is used to motivate mechanistic explanations for the occipital MI increase. Without age-specific diffusion evidence, the tractography result should be framed more cautiously as a putative anatomical scaffold.\n\"The Human Connectome Project consortium led by Washington University, University of Minnesota, and Oxford University is undertaking a systematic effort to map macroscopic human brain circuits and their relationship to behavior in a large population of healthy adults.\" ([4](https://pubmed.ncbi.nlm.nih.gov/23684880/))\nThis statement establishes that the Human Connectome Project (referenced by the paper’s HCP template URL naming) is designed around healthy adults rather than children. If the diffusion template used for streamline reconstruction is derived from HCP-style adult datasets, it is not a developmental diffusion atlas and does not encode pediatric white-matter organization. Therefore, using such data to support claims about “ongoing development” from ages 1–21 is a mismatch between data provenance and the biological phenomenon being inferred. Adult population-averaged streamlines can differ from pediatric tract structure and do not capture maturational changes in tract endpoints, pruning, or microstructure. This does not invalidate the existence of the named tracts, but it does weaken developmental inferences about their role in MI changes. The quote thus supports the critique that the tractography evidence is not developmentally grounded.\n\"Here we report an expert-vetted, population-averaged atlas of the structural connectome derived from diffusion MRI data (N = 842).\" ([3](https://pubmed.ncbi.nlm.nih.gov/29758339/))\nThis sentence clarifies that the referenced connectome resource is population-averaged rather than individualized. Population averaging can be valuable for illustrating canonical tract anatomy, but it is not a substitute for subject- and age-specific tractography when the research question is developmental change. In the reviewed paper, the key tractography claim is not merely anatomical presence but a developmental co-growth mechanism linking cortical MI changes across regions. A population-averaged atlas cannot test whether individuals with steeper occipital MI slopes also show corresponding tract differences, nor whether tract properties change with age in the relevant range. Thus, this quote supports the argument that the tractography portion is not evidentially aligned with the paper’s developmental interpretation. It reinforces that the tractography should be presented as a contextual visualization rather than causal/mechanistic support.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|GPT|4", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "The paper’s primary outcome (developmental change in MI as phase–amplitude coupling) is computed and interpreted without reporting key controls (e.g., surrogate testing, checks for non-sinusoidal waveform-driven coupling, or artifact-related harmonic coupling), which can produce spurious MI and threaten the validity of the developmental MI conclusions (Validity; Data and methodology; Conclusions).\n\n\"At each artifact-free nonepileptic site, we used the EEGLAB winPACT toolbox (https://sccn.ucsd.edu/wiki/WinPACT; Miyakoshi et al., 2013) to automatically compute MI; this program transforms all iEEG data points into Hilbert spectra and quantifies the strength of coupling between HFO amplitude and the instantaneous phase of slow waves.\"\nThis sentence describes the computational pipeline (Hilbert-based transforms with an automated MI computation) but does not mention any validation steps to ensure that the measured coupling reflects physiological cross-frequency interaction rather than signal-shape or spectral-leakage artifacts. In PAC analyses, Hilbert-based methods can yield non-zero coupling values even when apparent coupling is produced by non-sinusoidal slow waves, sharp transients, or harmonics rather than genuine modulation. Because the paper’s key claims hinge on spatial and developmental differences in MI, any systematic difference in waveform shape across age/region could masquerade as MI change. The manuscript also does not report surrogate-based normalization (e.g., phase shuffling) in the Methods section shown, which is commonly used to establish that MI exceeds what is expected under a null of no coupling. Without such safeguards, it is unclear how much of the reported occipital MI enhancement reflects true physiological PAC.\n\"Below, we report the normative developmental changes primarily in MI≥80 Hz & 0.5−1 Hz (Fig. 2), which is considered a surrogate marker of the delta-nested HFO that are believed to underly consolidation of long-term memory related to given sensory representations\"\nThis sentence goes beyond measurement and assigns a specific functional interpretation (“surrogate marker” for a memory-related physiological mechanism) to the MI estimate. Such interpretations require strong assurance that the MI metric is not inflated by non-neural artifacts or by waveform properties unrelated to cross-frequency interaction. Because the paper’s MI is computed on invasive clinical recordings in epilepsy patients, it is particularly important to demonstrate that sharp transients, harmonics, and residual epileptiform activity outside labeled zones are not driving MI. The paper later acknowledges that physiological HFO can “inflate” MI in occipital cortex, which further underscores the need to separate genuine coupling from properties like event rate and waveform morphology. Without explicit controls, the developmental changes in MI could partly reflect age-related changes in signal morphology or detector sensitivity rather than developmental strengthening of PAC. Therefore, the paper’s conclusions that MI-based coupling “is strengthened during development” are not sufficiently supported by the described methodology.\n\"Neuronal oscillations with Non-sinusoidal Morphology Produce Spurious Phase-to-Amplitude Coupling\" ([5](https://pubmed.ncbi.nlm.nih.gov/27597822/)).\nThis title and the associated abstract explicitly document that non-sinusoidal waveform morphology can generate spurious phase–amplitude coupling estimates. This is directly relevant because the reviewed paper’s MI is computed from Hilbert-based spectra of slow waves and HFO amplitude, a setting in which waveform asymmetries and harmonics can bias coupling metrics. The risk is especially salient in sleep iEEG, where slow waves can be highly non-sinusoidal and vary by region and age. Therefore, the reviewed paper should report diagnostic checks (e.g., waveform-shape metrics, harmonic/bicoherence assessments, or surrogate controls) to demonstrate that MI differences are not explained by non-sinusoidal morphology. The absence of such reporting leaves open a plausible alternative explanation for the observed developmental and occipital MI patterns. This undermines the validity of interpreting MI changes as strengthened physiological coupling.\n\"it remains unclear to what extent PAC may reflect spurious cross-frequency coupling induced by physiological artifacts or rhythmic non-sinusoidal signals with higher harmonics.\" ([6](https://pubmed.ncbi.nlm.nih.gov/33338621/))\nThis sentence from the broader PAC literature highlights two concrete confounds—physiological artifacts and non-sinusoidal harmonics—that can produce spurious PAC. The reviewed paper does not describe analyses that would specifically test for these confounds (e.g., distinguishing harmonic vs non-harmonic PAC, or quantifying spectral leakage/harmonicity), yet it uses MI as a core developmental biomarker. Because the main claims are regional (occipital vs others) and developmental (age dependence), any systematic regional or age-related difference in harmonic content could bias MI in the same pattern the paper attributes to development. This literature quote therefore directly motivates the need for additional controls that are not documented in the Methods section. Without addressing these established PAC pitfalls, the paper’s MI-based developmental conclusions remain vulnerable to alternative explanations. This is a major issue because MI is the central signal used to construct the principal atlas and mechanistic narrative.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "The submission relies on a protected MATLAB file (`MI_HFO_function.p`) for its core analysis, which prevents peer review of the methodology and hinders reproducibility.\n\n```matlab\nMI_HFO_function(fontsize,max_age,movie_time_range,Export_Movie,frame_number,Export_Fig,Snapshot_time,Tract1,Tract2,savename);\n```\nThe main analysis script `code.m` calls `MI_HFO_function`, which is provided as a P-code file (`MI_HFO_function.p`) in the `code/MI_HFO/demo_code/` directory. P-code files are obfuscated, executable-only files in MATLAB. This prevents reviewers and readers from inspecting the actual implementation of the Modulation Index (MI) and High-Frequency Oscillation (HFO) detection algorithms, making it impossible to verify the correctness of the code or reproduce the results from source.\n\"The analysis codes are available at https://github.com/kaz1126/flatten_map_and_tractography.\"\nWhile the supplementary material mentions a GitHub repository, the code provided in the submission package itself is obfuscated. For a paper claiming to provide a \"normative atlas\" and \"publicly available data\" [[1]](#ref1), full transparency of the processing pipeline is essential. The reliance on a \"black box\" function for the central analysis undermines the scientific validity and reproducibility of the study.\n\nReferences:\n[1] S. Petkoski et al., \"Developmental atlas of phase-amplitude coupling between physiologic high-frequency oscillations and slow waves,\" Preprint.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "The study normalizes electrode locations from infants (as young as 1 year) to an adult brain template (`FSaverage`), which introduces significant spatial errors due to the non-linear developmental changes in cortical folding and surface area.\n\n\"In order to pool sites from all patients, it was necessary to normalize the electrode locations to the standardized FSaverage brain surface (http://surfer.nmr.mgh.harvard.edu).\"\nThe `FSaverage` template is derived from adult brains. Mapping infant brains, which have significantly different gyrification patterns, surface areas, and brain volumes, to this adult template is known to introduce substantial spatial distortions [[2]](#ref2). The paper mentions using Infant FreeSurfer for reconstruction but then maps everything to the adult `FSaverage` for the atlas. This likely results in mislocalization of electrode sites, particularly in regions with high developmental plasticity, thereby compromising the accuracy of the proposed \"developmental atlas\".\n\"For patients younger than two, we used the Infant FreeSurfer software package to reconstruct the surface image\"\nWhile the reconstruction uses an age-appropriate tool, the subsequent normalization to an adult template negates this benefit for the group-level atlas. The spatial correspondence between a 1-year-old brain and an adult brain is not linear or simple, and using a standard adult surface registration for such a wide age range (1.0 to 41.5 years) without a specific pediatric template or more advanced registration method is a major methodological weakness.\n\nReferences:\n[2] A. Ghosh et al., \"Evaluating the validity of volume-based and surface-based brain image registration for developmental cognitive neuroscience studies in children 4 to 11 years of age,\" Neuroimage, vol. 53, no. 1, pp. 85–93, 2010. [https://pubmed.ncbi.nlm.nih.gov/20451621/](https://pubmed.ncbi.nlm.nih.gov/20451621/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "The study's conclusions regarding \"HFO\" developmental changes are heavily dependent on the specific detector used (Hilbert), with other detectors (MNI) showing contradictory results, suggesting that the \"HFOs\" in the occipital lobe may represent continuous physiological high-frequency activity rather than discrete events.\n\n\"HFO MNI ≥80 Hz rate was very low in the occipital lobes throughout all ages; this MNI method-specific observation can be attributed to its detector being designed to be agnostic to persistent forms of high-frequency activity\"\nThe authors acknowledge that the MNI detector, which is designed to detect discrete events and ignore continuous activity, finds very low HFO rates in the occipital lobe. This directly contradicts the findings from the Hilbert detector, which shows enhancement. This discrepancy suggests that the signal driving the \"HFO\" results in the occipital lobe is likely continuous high-frequency activity (high gamma), not discrete HFOs [[3]](#ref3).\n\"HFO HIL ≥80 Hz mixed model effect: +1.8 [95%CI: +1.7 to +1.9]; uncorrected p-value: < 0.001\"\nThe paper builds its main narrative around the Hilbert detector results (\"HFO HIL ≥80 Hz rate was physiologically enhanced\"). However, by conflating continuous high-frequency activity with \"HFOs\" (which are typically defined as transient events in epilepsy literature), the paper introduces terminological ambiguity. If the phenomenon is continuous, it should be characterized as such, rather than being presented under the umbrella of \"HFOs\", which implies a specific type of transient event often associated with pathology.\n\nReferences:\n[3] S. Ray and J. H. Maunsell, \"Different origins of gamma rhythm and high-gamma activity in macaque visual cortex,\" PLoS Biology, vol. 9, no. 4, p. e1000610, 2011. [https://journals.plos.org/plosbiology/article?id=10.1371/journal.pbio.1000610](https://journals.plos.org/plosbiology/article?id=10.1371/journal.pbio.1000610)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "The manuscript reports uncorrected p-values for key findings in the text, despite stating a policy of using FDR correction, which makes it difficult to assess the true statistical significance of the results given the multiple comparisons involved.\n\n\"We considered an FDR-corrected p-value of less than 0.05 as significant, for comparisons of six iEEG measures.\"\nThe Methods section establishes a threshold based on False Discovery Rate (FDR) correction. This is appropriate given the multiple measures and regions tested.\n\"HFO MNI ≥80 Hz mixed model effect: -0.044 [95%CI: -0.90 to +3.0 x 10⁻³]; uncorrected p-value: 0.067\"\nIn the Results section, the authors consistently report \"uncorrected p-value\". For example, the p-value of 0.067 is reported as uncorrected. It is unclear if the \"significant\" findings (e.g., p < 0.001) remain significant after FDR correction, or if the authors are selectively reporting uncorrected values to claim trends. Standard practice requires reporting the corrected p-values or explicitly stating which values survived the correction threshold defined in the Methods.\n\"The Spearman correlation failed to demonstrate a significant correlation between this regression slope and patient age in any lobe (uncorrected p-value: >0.05).\"\nReporting uncorrected p-values > 0.05 is fine to show non-significance, but for significant claims, the lack of corrected values is problematic.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Gemini|5", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "The authors claim that the observed increase in occipital MI implies a strengthening of visual memory consolidation, which is an unsupported leap from structural/electrophysiological data to cognitive function without any behavioral assessment.\n\n\"Given that occipital delta-nested HFO are believed to support visual memory consolidation, our observations imply that process may be significantly strengthened during early childhood.\"\nThis conclusion is based entirely on the observed increase in Modulation Index (MI) and structural connectivity (white matter tracts). The study did not perform any memory tasks or behavioral assessments. Inferring a functional cognitive change (\"process may be significantly strengthened\") solely from resting-state/sleep electrophysiology and structural MRI is speculative. While the authors phrase it as an implication, it is presented as a major conclusion of the study (\"Our study suggests that...\").\n\"one possible explanation for the developmental enhancement of occipital MI is that the cerebral cortex learns to generate HFO... optimizing visual memory consolidation\"\nWhile this is a valid hypothesis for discussion, presenting it as a primary explanation for the atlas features oversteps the data. Alternative explanations, such as simple maturation of local inhibitory networks or changes in skull conductivity/geometry affecting signal properties, are not sufficiently ruled out to prioritize a specific cognitive function like \"visual memory consolidation\" [[4]](#ref4).\n\nReferences:\n[4] G. Buzsáki and F. L. da Silva, \"High frequency oscillations in the intact brain,\" Progress in Neurobiology, vol. 98, no. 3, pp. 241–249, 2012. [https://www.ncbi.nlm.nih.gov/pmc/articles/PMC3429666/](https://www.ncbi.nlm.nih.gov/pmc/articles/PMC3429666/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "The interpretation of MI as indicator for visual memory consolidation is somewhat speculative: The visual memory consolidation was not tested in these patients but only inferred from the literature. The conclusions with respect to epilepsy surgery should be more cautious.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "The iEEG figures must be improved. All the values given in the legend should be presented in a table and not in the figure panel.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "The authors use the same y-axis in all plots for better comparison across brain areas. This puts many points close to y=0 so that they cannot be discerned. I suggest a log10 y-scale combined with a log10 x-scale. Then the fit of a power law will appear as a straight line with the slope being the exponent. Given the three linear regressions used in this study (age, square root of age, and log10 age), this will be more illustrative. At the same time, it will allow a visual judgement of the regression, which is not possible now for many subplots.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "The three patients >20years appear as outliers. Please redo all analyses without these three patients to verify that you results are valid for your core set of patients, which is aged \\( \\leq 20 \\) years.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "The authors record iEEG with 1000 Hz. This precludes analysis of spectral content >250Hz. All their text on HFO >250Hz (Fast Ripples) is unfounded speculation not based on their data. This text should simply be removed.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "Please read the reference (Zweiphenning et al., 2022a) closely and summarize it correctly. The current summary is wrong.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "Please remove the older reviews on HFO and replace them by (Chen Z, Maturana MI, Burkitt AN, Cook MJ, Grayden DB. High-frequency Oscillations in Epilepsy: What Have We Learned and What Needs to be Addressed. Neurology. 2021. https://doi.org/10.1212/wnl.0000000000011465). I recommend reading that review closely. While the study analyses four types of HFO for which detectors are available in the toolbox, their value for epilepsy surgery is still debated.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "While the conclusions regarding epilepsy appear in the abstract, they should be made explicit at the end of the manuscript. Of course, they must be cautious and limited to the data provided in this study. Explicit conclusions will help the reader to understand the noteworthiness of the study.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "The writing is generally good, but I believe it can be much more structured (adhering strictly to intro-methods-results sections and use the same structures within). I will mention some examples in my comments below.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "Sentences can be shorter. E.g., words like ‘only’ or ‘in this study’ are often redundant and words like ‘as well as’ can be shortened to ‘and’", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "Abstract/manuscript: iEEG included only subdural (electrocorticography) recordings. This should be specified, already in the abstract", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "Introduction: ‘independent effects of patient and epilepsy profiles’: how is epilepsy profiles an independent effect? I could not find the definition of ‘epilepsy profiles’ in methods, but it is used several ties in abstract, introduction and results.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "Introduction: ‘In addition to modeling cortical ontogenic changes, the present study also visualized 140 white matter pathways supporting the development of neural communications via delta141 nested HFO (as rated by MI≥80 Hz & 0.5-1 Hz), during slow-wave sleep. To accomplish this, we 142 utilized our novel imaging technique, dynamic tractography, which combines iEEG signals 143 with MRI tractography’ This is a methods-like description while in the introduction I want to hear why this extra step was taken and why the specific methods.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "Methods: a sample rate of 1000 Hz is low to recognize HFOs>250 Hz", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "Methods/results: the methods describe that 114 patients will be selected and then the inclusion criteria. I want to know how these 114 patients resulted from how many patients in the beginning. It seems that the period is the strict criterium, so than 114 patients is a result from the selection.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "Methods/results: To ensure the accuracy of the developmental iEEG 192 atlases, we only included artifact-free iEEG segments from 8,251 nonepileptic electrode sites 193 (mean: 72.4 per patient; range: 12 to 121;) Here again, the number of used/selected channels is a result. I want to know how many channels were discarded because of artefacts, SOZ, MRI, irritative zones.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "survived an FDR correction (for 18 comparisons: six iEEG measures × three types of age measures): I wonder if an FDR is really needed here because both the iEEG measures and the types of age measures are dependant variables. It is good to reduce the change of finding false positive relations but high correction for false discoveries may yield false negative results. This should be discussed in the discussion (Wagenmakers E et al Nature 2022 one statistical analysis must not rule them all).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "I have to two main criticisms to this work: 1. the absence of analysis on the pathological channels and the claim of a better definition of the EZN\\n2. the lack of evidence supporting the hypothesis that visual memory consolidation and the strengthen of the MI in the occipital lobe are linked\\n\\nI suggest dedicating more place in the paper to the neurocognitive aspect and the hypothesis possibly associated with this finding than to the need of improving the epileptogenic biomarkers. Indeed, the HFO and MI analysis is done on the “physiological” channels, so no information is done on the real identification of the EZN in these patients. If you claim this, you should also analyse the epileptogenic channels.\\n\\nFor example, in the abstract and introduction you mention that this atlas could improve the “age-appropriate localization of the epileptogenic zone”, I’m not sure that your results can assure this, it is more an adding information on physiological developmental activities as no data support a better delineation of the EZN in these patients.\\n\\nFrom a practical point of view, I find difficult to use these results in the clinical practice for the definition of the epileptogenic zone, but they are really important for the understanding of the visual memory process. As mentioned in the paper, HFO in the occipital lobe are found at a very high frequency rate in the physiological brain and it is difficult to use these markers for the definition of the EZN in this area.\\n\\nThe authors analysed a large cohort of patients (n=114) including very young children (n= 14 < 4 years old) studied by iEEG and operated with an Engel class I in the follow up. The brain area analysed were the “physiological” ones, so the ones not involved in the EZN.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "It will be of interest to compare the MI in the “physiological” occipital lobe with the MI in the “pathological” ones and possibly with neuropsychological evaluations. Does it exist a “threshold” of MI that distinguishes the physiological from pathological channels? Do neurophysiological data correlate with neuropsychological examination?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "If MI is involved in visual memory consolidation, children with visual memory impairment may possibly show modifications in this index. I think more data is needed to support your hypothesis on visual memory.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "I found it limiting not to define better the criteria of \\\"slow wave sleep\\\". In animals, there is no clear consensus but in humans, it should correspond to the criteria of slow wave sleep N3 according to the AASM (American academy of sleep medicine) and specify if it is the first or second part of the night at least because the proportion of slow waves is not the same. It would also be necessary to specify on which way they determined the stage of sleep, knowing that the amplitude of the slow waves can be different according to the regions.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "Data are collected during sleep; do you think that dreams rather than the sleep modifications during this early stage of life can play a role? Did you look to spindles activities? Could be MI involved in such a change? Occipito-parietal regions are also taught to be involved in consciousness (Siclari et al., Nat Neurosci 2017), do you think your findings could be somehow linked to such experiences in the young child?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "It seems that the mesial part of the fronto-parietal lobes behaves differently from the lateral ones, did you try to separate these areas in your statistical analysis? In particular, hippocampus is known to have physiological ripples especially during sleep involved in memory processing, so maybe it deserves a different approach that being included in all the temporal lobe.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Human_3|7", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "Limitations are represented by the subdural iEEG technique that evaluates more the cortical aspects of the brain, without a good sampling i.e. of the mesial temporal regions that are fundamental for memory consolidation; this limits to me the word “global atlas” because some important regions are not sufficiently sampled.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Human_3|8", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "I could not find the ancillary analysis of the rates of HFO>150 hz and 250 Hz that could indeed be of interest regarding the difference between pathological and physiological HFO even if done on a smaller cohort of patients.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Human_3|9", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "Regarding occipital HFA independently of epileptogenic area, you can cite also Melani 2013 Continuous High Frequency Activity: A peculiar SEEG pattern related to specific brain regions.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|24|Human_3|10", "source": "prb", "split": "test", "paper_id": "prb24", "comment": "What do you mean with the word “enhanced MI?” could you better clarify?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Claude|1", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "The paper introduces the sparse-wave vs. dense-wave distinction as a central contribution, but the comparison between these two regimes involves simultaneous changes in network size (from 12,500 to 1,012,500 neurons), connections per neuron (from 100 to 3,000), and synaptic conductances (Ge from 4nS to 1nS, Gi from 0.49nS to 10nS), making it impossible to isolate the contribution of any single factor to the emergence of sparse participation in traveling waves.\n\n\"This randomly-connected network generated self-sustained activity with spontaneous spiking fluctuations consistent with the asynchronous-irregular regime and lacked any spatiotemporal structure (Fig. 2b).\"\nThe paper describes the sparse-wave network (1,012,500 neurons) in detail, but when comparing to the dense-wave network, multiple parameters are changed simultaneously, preventing attribution of the sparse participation specifically to network scale versus other factors.\n* Quote from Supplementary Table S1: \"Dense Network: N_Neurons = 12,500, N_Synapse/Neuron = 100, G_e = 4e-9, G_i = 490e-9\" vs \"Topographic Network: N_Neurons = 1,012,500, N_Synapse/Neuron = 3000, G_e = 1e-9, G_i = 1e-8\"\nThis table reveals that the dense-wave network has 80x fewer neurons, 30x fewer synapses per neuron, 4x higher excitatory conductance, and roughly 50x higher inhibitory conductance than the sparse-wave network. These differences span multiple orders of magnitude across several parameters, making it methodologically problematic to conclude that sparse participation emerges specifically due to network scale. Standard practice in computational neuroscience would be to vary parameters systematically while holding others constant to establish causality.\n\"If it were the case that neurons strongly participated in these fluctuations, then they would show a degree of coherence in the range of frequencies dominated by those fluctuations. To demonstrate this, we simulated a smaller network with fewer neurons and denser connections which generated spontaneous fluctuations that strongly regulated spiking activity.\"\nThis statement acknowledges that the dense-wave network was intentionally designed with different parameters to produce different dynamics, but it does not address whether sparse participation could be achieved in smaller networks with appropriately tuned parameters, or conversely, whether dense waves could emerge in large networks with different conductance values.\nFrom [Kumar et al. 2008, The high-conductance state of cortical networks](https://doi.org/10.1162/neco.2008.20.1.1): \"We show that the high-conductance state can emerge self-consistently in a recurrent cortical network model if the synaptic weights are chosen correctly.\"\nPrevious literature establishes that the emergent dynamics in spiking networks depend critically on the balance of synaptic conductances. Given the substantial differences in conductance values between the sparse and dense networks in the paper under review, the observed difference in wave participation could be primarily driven by conductance ratios rather than network size, undermining the central claim about scale-dependent sparsity.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Claude|2", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "While the paper claims that \"The model recapitulated the distribution of traveling wave speeds and wavelengths observed in marmoset area MT,\" the comparison between model predictions and experimental data in Figure 4 relies solely on visual inspection of histograms without formal statistical tests to quantify the degree of agreement between the distributions.\n\n\"The speed of waves in the topographic network (Figure 4a, 0.26 ± 0.05 m/s, mean ± S.D.) was well-matched to the speed in marmoset area MT (Figure 4b, 0.34 ± 0.14 m/s).\"\nThe paper reports mean and standard deviation values but does not perform any formal statistical comparison between the model and experimental distributions. The model mean (0.26 m/s) differs from the experimental mean (0.34 m/s) by approximately 30%, and the experimental standard deviation is nearly 3x larger than the model standard deviation, yet no statistical test (such as a Kolmogorov-Smirnov test, Mann-Whitney U test, or similar) is reported to assess whether these distributions could have arisen from the same underlying process.\n\"As in the cortical recordings, instantaneous wavelengths tended to be between 2 and 4 mm, with a peak wavelength at ~3 mm in both the model (Fig. 4c) and marmoset area MT (Fig. 4d).\"\nThis statement relies on qualitative pattern matching (\"tended to be,\" \"with a peak at\") rather than quantitative statistical comparison. While the histograms in Figure 4c-d appear visually similar, the lack of formal statistical testing means readers cannot assess whether the apparent similarity is statistically significant or could arise by chance given the sample sizes and variability.\nFrom [Brunel 2000, Dynamics of sparsely connected networks](https://doi.org/10.1023/A:1008925309027): \"We investigate analytically and numerically the dynamics of networks of sparsely connected excitatory and inhibitory integrate-and-fire neurons.\"\nIn contrast to the detailed analytical and numerical validation approaches used in foundational work on spiking network models, this paper's comparison to experimental data lacks the rigor needed to establish that the model captures the essential features of cortical traveling waves. Without quantitative statistical validation, the claim of correspondence remains qualitative.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Claude|3", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "The paper uses a simplified LFP proxy based on summed synaptic currents that explicitly excludes spatial mixing (signal pooling across adjacent neuronal pools), but states without systematic demonstration that \"our results do not depend critically on the choice of LFP proxy.\"\n\n\"This LFP proxy is then computed for each 10 x 10 neuron pool across the two-dimensional network. This proxy was initially computed independently for each neuron pool, excluding effects from mixing of the LFP signal across space.\"\nThe paper acknowledges that spatial mixing is excluded from the LFP calculation. Since traveling waves are fundamentally spatial phenomena and their detection depends on phase relationships between spatially distributed recording sites, excluding mixing effects could artificially enhance apparent wave organization in the model.\n\"We note that excluding these effects is a conservative step, as the addition of the mixing across space would only increase traveling waves in the LFP.\"\nThis assertion is presented without supporting evidence or citation. While intuitive, spatial mixing could also blur phase relationships and potentially either increase or decrease detected wave organization depending on the spatial scale of mixing relative to the wavelength. The claim that mixing would \"only increase traveling waves\" requires demonstration.\n\"Further, we note that our results do not depend critically on the choice of LFP proxy and our conclusions are unchanged when analyzing the mean membrane potentials or excitatory synaptic conductances.\"\nThis claim is made but not systematically demonstrated in the paper. No supplementary analysis is provided comparing wave detection results across different LFP proxies. Given that the Mazzoni et al. (2015) method cited for the LFP calculation was validated for different purposes than traveling wave detection, this claim requires empirical support.\n* Quote from [Mazzoni et al. 2015, Computing the Local Field Potential from Integrate-and-Fire Network Models](https://doi.org/10.1371/journal.pcbi.1004584): \"Our results demonstrate that the low-pass filtering hypothesis is appropriate for the LFP... and suggest caution when interpreting high-frequency components.\"\nThe original Mazzoni et al. paper validated their LFP proxy primarily for capturing low-pass filtered population dynamics and temporal power spectra, but did not specifically validate it for spatial phase gradient calculations used in traveling wave detection. The application of this proxy for wave analysis represents an extension beyond its original validated use case.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Claude|4", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "The paper uses specific threshold criteria for wave detection (wavelength exceeding the 99th percentile of shuffled data) but does not explore how sensitive the reported wave statistics are to the choice of detection thresholds, which could affect the conclusions about wave prevalence and properties.\n\n\"We then identified places and times in the network where the organization of activity into traveling waves was significant, defined as times when the wavelength exceeded the 99th percentile of the time-shuffled data\"\nThe choice of the 99th percentile as the threshold for significance is reasonable but arbitrary. The paper does not report how the percentage of time spent in wave states, the mean wave properties, or the comparison to experimental data would change if different thresholds (e.g., 95th or 99.5th percentile) were used. This sensitivity analysis is important because the main conclusions about wave prevalence depend on this threshold.\n* Quote from code (gradient_measure.m): \"p = sum( (1./pm(:)) > prctile(1./pm_sh(:),99) ) ./ numel( pm(:) );\"\nThe code confirms that the 99th percentile threshold is hardcoded into the analysis pipeline. While the code also calculates an alternative measure based on 3σ of the connectivity Gaussian, neither this alternative nor variations in the percentile threshold are reported in the paper. Standard practice would include reporting results across a range of thresholds to demonstrate robustness.\n\"The spatial correlation of the spiking activity (Fig. 3f) was increased in the topographic network (0.54) compared to the random network (0.03), similar to spatial correlation in LFP amplitude during detected waves in marmoset area MT (0.31).\"\nThe spatial correlation values for the model (0.54) and experimental data (0.31) differ by 74%, which is substantial. Without sensitivity analysis of detection parameters, it is unclear whether this difference reflects a genuine model-data discrepancy or could be reduced with different threshold choices for wave detection.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|GPT|1", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "This paper makes a mechanistic claim that spontaneous traveling waves observed in awake cortex are generated by (and even are a necessary consequence of) distance-dependent horizontal-fiber conduction delays, but the manuscript’s evidence only establishes that such delays are sufficient in a particular model class and does not justify the stronger causal/necessity conclusion for cortex.\n\n\"Importantly, this model incorporated axonal time delays from conduction along unmyelinated horizontal fibers, which shaped ongoing activity patterns into traveling waves consistent with those observed in vivo.\"\nThis sentence describes a model-based sufficiency result (a model component \"shaped\" activity into waves) but is phrased as if it explains the biological mechanism. In computational neuroscience, demonstrating that a mechanism can produce an observed phenomenon is not the same as showing it is the operating mechanism in the brain. The manuscript does not present a causal perturbation or direct measurement tying horizontal-fiber delays to the recorded waves (e.g., selectively disrupting horizontal propagation or measuring conduction-delay distributions in the same preparation). Because multiple circuit and measurement mechanisms can produce propagating LFP patterns, the inference requires additional constraints beyond qualitative similarity. Without such constraints, the conclusion risks being underdetermined by the presented evidence.\n\"Thus, not only are spontaneous traveling waves consistent with the asynchronous-irregular regime, they are a necessary consequence of topographic connectivity and time delays in cortex across conditions that yield asynchronous-irregular spiking.\"\nThe phrase \"necessary consequence\" is a very strong claim that goes beyond what the results section (as summarized in the manuscript) actually establishes. The reported scans demonstrate wave prevalence within a chosen model family and chosen definitions of asynchronous-irregular activity, but necessity would require ruling out alternative biophysical or network mechanisms and showing that removing the hypothesized element abolishes waves across plausible models and measurement models. The manuscript does not present such a falsification argument for cortex; it mainly compares model outputs to recordings and explores parameter robustness within the same modeling framework. It is also logically inconsistent to claim necessity in cortex while the paper acknowledges that traveling waves can occur in models without distance-dependent delays (even if in restricted ranges). In short, the claim is stronger than warranted by the presented results.\n\"Our modeling results suggest that the spontaneous LFP fluctuations we observe traveling as waves in the cortex during active vision result from sparse waves of spiking activity traveling unmyelinated horizontal fibers.\"\nThis sentence explicitly moves from a model proposal to a biological causal statement (\"result from\"), but the manuscript does not provide a unique identification argument. Matching speeds to putative conduction velocities (and matching some summary statistics) is not sufficient to uniquely identify horizontal-fiber conduction delays as the cause, because other mechanisms can generate waves at similar scales and apparent speeds depending on filtering and spatial mixing. Moreover, the biological recordings used here are LFP-based, and LFP wave properties can change with the forward model of signal generation and electrode integration. A stronger claim would require triangulating with additional observables that are specifically diagnostic of horizontal conduction delays (e.g., delay-vs-distance relationships in effective connectivity). As written, the paper’s conclusion overreaches relative to its evidence.\n```text\nTo test whether topographic connections with transmission delays were sufficient to generate spontaneous traveling waves in the network, as a refinement to the model described in Figure 2a, two key elements were introduced: 1) connection probability decayed as a Gaussian with distance between neurons (\\( \\sigma = 400 \\) \\( \\mu \\)M)\\(^{39,40}\\) to mimic the topographic connectivity in cortex and 2) action potentials activated synaptic currents after a time delay determined by the distance of the connection to simulate the conduction velocity of horizontal fibers in cortex (\\( v_c = 0.2 \\) m/s,\\(^4\\)\n```\nThis passage frames the key manipulation explicitly as a test of \"sufficient\" conditions, not of necessity, and it stays within a particular stylized network construction. The methodological framing underscores that the strongest justified conclusion from these experiments is sufficiency within that model family. Elevating a sufficiency demonstration to a necessity claim about cortex would require additional controls (e.g., models with realistic laminar structure, alternative propagation mechanisms, and/or direct perturbation evidence). In addition, because two elements are introduced together (topography and distance-dependent delays), the manuscript’s design does not isolate which properties of the combination are essential for the specific phenomenology in the model. As a result, the causal chain from delays to waves to in vivo interpretation remains suggestive rather than established.\n\"We include a delay time ![](article/file?type=thumbnail&id=10.1371/journal.pcbi.1000611.e080) into the interactions between neurons. For simplicity, we chose ![](article/file?type=thumbnail&id=10.1371/journal.pcbi.1000611.e081); our results do not depend sensitively on these values.\" ([3](https://journals.plos.org/ploscompbiol/article?id=10.1371/journal.pcbi.1000611))\nThis literature statement illustrates that propagating spatiotemporal patterns can arise in spiking networks without fine-tuned or strongly determining delay structure, at least in some modeling contexts. While the models differ from the present manuscript, it directly undermines the rhetorical move from “including conduction delays produces waves” to “distance-dependent delays are necessary.” It also highlights that, in the broader literature, delays are often one of multiple modeling ingredients rather than a uniquely identifying cause. Therefore, the present paper’s strongest defensible stance is that distance-dependent delays are a plausible and sufficient mechanism in a particular biologically motivated model family. Using a necessity framing (especially in cortex) is not supported by the level of evidence provided.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|GPT|2", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "This paper’s key claims rely on large-scale simulations and parameter scans, but the provided materials (as described in the manuscript and code) do not provide a fully specified, versioned, end-to-end pipeline (simulator version, parameters, seeds, compute requirements, and outputs) that would allow an independent group to reproduce the main quantitative results.\n\n\"Simulations were generated using a specialized program called NETSIM, which is approximately 1,500 lines of C code (available at http://mullerlab.github.io).\"\nThis sentence indicates that the main simulation engine is an external software dependency rather than being self-contained within the manuscript’s accompanying code package. For reproducibility, it is not enough that software is generally “available”; independent replication typically requires a specific version (commit hash/release), build instructions, and a record of relevant compiler flags and platform assumptions. The manuscript does not specify a versioned NETSIM snapshot that corresponds to the reported results, which creates ambiguity because simulation engines evolve and numerical details can change. The paper also reports extensive sweeps and comparisons, which are particularly sensitive to implementation and parameter defaults. As written, an independent reader cannot be confident they would reproduce the same quantitative figures from the stated materials.\n\"In order to run these simulations across all combinations of network size and conductance parameters, we utilized the Extreme Science Engineering Discovery Environment (XSEDE) Comet cluster at the San Diego SuperComputer (SDSC) center at UC San Diego.\"\nThis statement signals that producing the central scan results required access to substantial HPC resources and a specific execution environment. That is not inherently a flaw, but it heightens the need to provide reproducible artifacts (job scripts, resource specifications, and outputs) because reproducing the full experiment becomes expensive and sensitive to environment differences. The manuscript does not provide a clear mapping from the scan description to a runnable workflow that an external lab could follow, including how failures, early-exit conditions, or random seeds were handled across thousands of runs. Without these details, the headline generality claims from the scan are difficult to independently verify. Common practice in large computational studies is to release the scan outputs (or sufficient summaries) alongside code to avoid forcing full recomputation.\n\"Our custom software implementation allowed for the simulation of networks with approximately 100,000 to 1,000,000 neurons, each with 3,000 synapses per cell, addressing in the largest networks over 60 GB of RAM.\"\nThis sentence quantifies the scale and memory requirements of the key experiments, underscoring that full reruns are nontrivial. When experiments are this resource-intensive, reproducibility standards typically expect that the authors provide either (i) the full set of outputs needed to regenerate figures/tables, or (ii) a reduced but faithful reproduction recipe that produces a representative subset of the key results. The code package in this benchmark includes analysis scripts but not an executable simulator implementation; the simulation engine is external and the large-scale outputs are not bundled. As a result, even well-resourced readers may be unable to confirm that the reported wave prevalence and matching statistics emerge as claimed. This gap directly affects the transparency of the paper’s central claims.\n\"The simulated data from this paper were generated with NETSIM (github.com/mullerlab/NETSIM), an efficient spiking neural network simulator written in C, capable of simulating dynamics of networks on the order of one million neurons on a local machine.\"\nThis repository statement confirms that the computational heart of the paper is delegated to an external simulator. However, it still does not resolve the core reproducibility issue: the exact simulator version and build configuration that produced the published figures are not pinned, and the full run/scan artifacts are not provided. In practice, even small simulator changes (numerical integration details, RNG behavior, default parameter parsing) can alter quantitative outcomes, especially near boundaries of dynamical regimes. This is particularly relevant here because the paper makes strong claims about robustness across parameter space and about precise wave statistics. Without a version-locked simulator and run scripts, these claims are harder to audit.\n```matlab\nfunction runNetsim(wd,param_pathfile,outputdir)\n\nparam_pathfile = GetFullPath(param_pathfile);\noutputdir = GetFullPath(outputdir);\n\nif ~exist(outputdir,'dir'), mkdir(outputdir); end\n\nparam_pathfile = strrep(param_pathfile,' ','\\ ');\noutputdir = strrep(outputdir,' ','\\ ');\n\ncd('./NETSIM')\nsystem('make clean');\nsystem('make COMPILE_TYPE=performance');\nsystem( sprintf( './netsim -f %s -o %s' , param_pathfile , outputdir ) );\ncd(wd)\n\nend\n```\nThis code block shows that reproducing simulations requires a separate `./NETSIM` directory and a compiled binary built via `make`, reinforcing the external dependency and environment sensitivity. The build is invoked without pinning to a specific NETSIM commit or recording compilation outputs, which makes exact reproduction fragile. It also illustrates that the intended workflow assumes a local build environment consistent with the authors’ setup; this may not hold across OS/compiler variations. For a paper whose main claims rest on simulator output, best practice would be to provide an archived, versioned simulator snapshot and a scripted workflow that can regenerate key figures from scratch (or provide archived outputs). In its current form, the code package is closer to “analysis scripts plus instructions” than a reproducible research artifact.\n\"In order to exactly reproduce a given result, it may be necessary to use programs in the exact versions used originally.\" ([1](https://journals.plos.org/ploscompbiol/article?id=10.1371/journal.pcbi.1003285))\nThis reproducibility guidance directly applies to the manuscript because its main simulator (NETSIM) is an external program and the results depend on it. The paper does not specify an exact NETSIM version (e.g., release tag or commit hash) used for the reported results, which makes exact reproduction uncertain. This is especially problematic in large parameter scans where subtle numerical differences can shift regime boundaries and summary statistics. The guideline also notes that even with recorded version numbers it can be nontrivial to retrieve old versions, reinforcing why an archived snapshot is preferable. Therefore, the paper’s current materials fall short of common reproducibility recommendations for computational work.\n\"Importantly, it is our intent that the principles apply not only to ‘data’ in the conventional sense, but also to the algorithms, tools, and workflows that led to that data.\" ([2](https://www.nature.com/articles/sdata201618))\nThis FAIR statement emphasizes that workflows and tools are first-class research objects that should be made reusable and transparent. The present paper’s computational pipeline depends on a simulator plus HPC execution context and many parameterized runs, which are precisely the kinds of “workflows” that need clear packaging to be reusable. While the authors provide MATLAB analysis code and parameter files, the end-to-end workflow (including simulator version, build, seeds, and full scan outputs) is not packaged in a way that supports straightforward reuse. This gap is not merely a documentation nuisance; it impedes independent validation of the paper’s main conclusions. Aligning with FAIR-style expectations would require making these computational research objects more findable and reusable.\n\"To run simulations and to enable reproducibility, NETSIM has a simple parameter file system, where an input file (with extension .parameters) is taken as input in the form “variable = value”.\" ([5](https://github.com/mullerlab/NETSIM))\nThis external documentation highlights that NETSIM is designed with reproducibility in mind via parameter files, which makes the lack of version pinning and end-to-end workflow release more striking. Parameter files alone do not guarantee reproducibility if the simulator version and RNG behavior are not fixed, or if the full set of parameter files used in large scans and their corresponding outputs are not provided. In this manuscript, the headline robustness claims derive from thousands of runs; reproducing those conclusions would typically require access to the complete set of scan inputs/outputs. Without those, an independent group must reconstruct the full sweep environment and hope that the same simulator version is used. The paper would be substantially stronger if it leveraged NETSIM’s reproducibility features by shipping a fully specified, version-locked reproduction package.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|GPT|3", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "The paper’s wave detection and model–data comparisons hinge on a specific simulated LFP proxy, but the provided MATLAB implementation applies a nonlinear absolute value and uses a conductance×driving-force form that does not match the manuscript’s stated linear LFP proxy; this discrepancy undermines the validity and reproducibility of wave/phase analyses.\n\n\"The LFP estimate \\( \\lambda(t) \\) is computed as a weighted sum of the excitatory and inhibitory synaptic currents \\( I_e \\) and \\( I_i \\) across \\( m \\) excitatory cells in each 10 x 10 neuron pool:\\n\\n\\[\\n\\lambda(t) = \\sum_j^m I_{e,j}(t - \\tau) - \\alpha \\sum_j^m I_{i,j}(t)\\n\\]\"\nThis defines a linear proxy in terms of synaptic currents with a signed combination of excitation and inhibition. The linearity and the sign structure matter because subsequent analyses (generalized phase, phase gradients, speed/wavelength estimates) assume a meaningful oscillatory signal with interpretable phase. If the actual implementation deviates materially (e.g., through nonlinear rectification), the computed phase structure and wave statistics can change. The manuscript also argues that waves traverse locally asynchronous-irregular dynamics and that spike-phase coupling matches in vivo; these claims are sensitive to how the LFP proxy is computed. Therefore, fidelity between the described proxy and the implemented proxy is important for validity.\n```matlab\ntime_shift_lfp = 0.006 ./ ( vars.dt * vars.record_downsample_factor );\nlfp = abs( circshift( ges.*(vars.Ee-vms), [0 time_shift_lfp] ) - 1.65*gis.*(vars.Ei-vms) );\n```\nThis code implements a nonlinear absolute value (`abs`) applied to the combined excitatory/inhibitory term, which is not present in the manuscript’s equation for \\(\\lambda(t)\\). Taking an absolute value is a rectification that changes the distribution and temporal waveform of the signal; after mean-subtraction it can still create negative values, but the nonlinear transformation can introduce harmonics and distort phase estimates. In addition, the code uses `ges.*(Ee-vms)` and `gis.*(Ei-vms)`, i.e., conductance multiplied by driving force, whereas the manuscript explicitly defines the proxy in terms of currents \\(I_e, I_i\\) and a signed weighted sum; the relationship may be close under some conventions, but it is not documented here and the additional `abs` makes it definitively different. Since wave detection in the manuscript is based on generalized phase and spatial phase gradients, any such distortion can alter wave prevalence, speeds, and coupling metrics. This mismatch creates uncertainty about whether the reported wave statistics correspond to the stated model.\n\"We note that excluding these effects is a conservative step, as the addition of the mixing across space would only increase traveling waves in the LFP.\"\nThis statement emphasizes that methodological choices in constructing the LFP proxy can systematically affect the presence and strength of traveling waves. Given that sensitivity, it becomes even more important that the code precisely matches the manuscript’s described proxy and that any deviations are justified. The released code’s rectification step is a major deviation that could change wave detectability and therefore the quantitative conclusion that waves occupy a given fraction of time and match in vivo distributions. The manuscript does not discuss applying a rectifying nonlinearity, so readers cannot assess whether results are robust to that choice. As a result, the paper’s claims about matching cortical wave statistics are less verifiable.\n\"Given that LFPs are generated by spatially separated currents across the neuronal membrane, they cannot be computed directly from quantities defined in models of point-like LIF neurons.\" ([4](https://journals.plos.org/ploscompbiol/article?id=10.1371/journal.pcbi.1004584#sec001))\nThis statement from the cited reference underscores that LFP proxies for point-neuron models are approximations whose exact form matters. Because the proxy is an approximation, it should be implemented and reported consistently so that others can replicate the analysis and evaluate sensitivity. The mismatch between the manuscript’s linear proxy and the code’s rectified proxy means that the paper is not currently providing a single well-defined computational observable for its core wave analyses. This is not a minor implementation detail: phase-based wave metrics are especially sensitive to nonlinear transformations. Therefore, the discrepancy undermines the transparency and interpretability of the model–data comparisons.\n\"Since the optimal values of *α*, ([Fig 5A](#pcbi-1004584-g005)) *τ*AMPA and *τ*GABA ([S2B Fig](#pcbi.1004584.s002)) were relatively stable across depths, we defined a new proxy: the reference weighted sum LFP proxy (RWS). The structure of the RWS proxy is the same as the WS proxy but the variables are fixed: *α* is set to the average accross depths of the optimal values for WS (1.65, see [Fig 5A](#pcbi-1004584-g005)) and the delays to *τ*AMPA = 6 ms and *τ*GABA = 0 ([S2C Fig](#pcbi.1004584.s002)).\" ([4](https://journals.plos.org/ploscompbiol/article?id=10.1371/journal.pcbi.1004584#sec001))\nThis reference text clarifies the intended proxy form: a fixed linear combination of AMPA- and GABA-related terms with specified delays and weights. Crucially, the reference does not motivate or include an absolute value rectification in the proxy definition. The current manuscript adopts the same numerical parameters (6 ms and 1.65) in its methods, suggesting it intends to follow the reference proxy closely. However, the provided implementation adds `abs`, creating a different proxy than the one justified by the cited literature. This divergence raises doubts about whether the reported wave and phase statistics correspond to the theoretically motivated proxy or to a modified one.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "The paper claims that the mechanism for spontaneous traveling waves was \"unknown\" and presents distance-dependent delays as a novel explanation. This ignores established theoretical work which has long demonstrated that delays in spatially extended networks can generate traveling waves.\n\n\"The underlying mechanism for these waves, however, is unknown.\"\nThis claim ignores a significant body of theoretical literature. The role of delays in generating spatiotemporal patterns, including traveling waves, has been extensively studied.\n\"Based on their speed of propagation, we hypothesize these waves result from action potentials propagating along unmyelinated horizontal fibers.\"\nWhile the specific biological substrate (horizontal fibers) is a valid hypothesis, the dynamical mechanism (distance-dependent delays causing waves) is not a new discovery of this paper.\n\"We show that... delays... lead to a variety of spatiotemporal patterns, including... traveling waves.\" [2]\nRoxin et al. (2005) explicitly demonstrated that in large networks of spiking neurons, distance-dependent delays can destabilize the asynchronous state and lead to traveling waves. The current paper's findings are a confirmation of this theoretical prediction in a more detailed model, rather than the discovery of a new mechanism.\n\nReferences:\n[2] Roxin, A., Brunel, N., & Hansel, D. (2005). Role of delays in shaping spatiotemporal dynamics of neuronal activity in large networks. Physical Review Letters, 94(23), 238103. https://journals.aps.org/prl/abstract/10.1103/PhysRevLett.94.238103", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "The paper claims that the observed traveling waves do not induce \"deleterious neuronal correlations\" and that pairwise correlations remain unchanged. This is mathematically inconsistent with the finding that these waves modulate excitability and spike timing, which necessarily implies the induction of pairwise correlations.\n\n\"without inducing changes in pairwise correlations in the activity of individual neurons.\"\nThis claim is problematic. If a traveling wave modulates the firing probability of neurons across the network, then any two neurons that are phase-locked to the wave (as shown by the Spike-Phase Index) must exhibit correlations in their firing times on the time scale of the wave period.\n\"These waves systematically modulate excitability across the retinotopic map, strongly affecting perceptual sensitivity\"\nThe authors admit that the waves modulate excitability. If excitability is modulated by a shared signal (the wave), then the output spikes of neurons receiving this signal will be correlated. Claiming that correlations are unchanged implies either that the modulation is negligible (contradicting the \"strongly affecting\" claim) or that the measurement of correlation was insufficient (e.g., averaged over too long a window or insensitive to the specific timescale of the wave).\n\"individual neurons sparsely participate in waves\"\nWhile sparse participation might reduce the *average* correlation, it does not eliminate it. The conditional correlation (given the presence of a wave) would be significant. Characterizing this regime as having \"no changes in pairwise correlations\" is misleading, especially since even weak correlations can significantly impact information coding [5].\n\nReferences:\n[5] Zohary, E., Shadlen, M. N., & Newsome, W. T. (1994). Correlated neuronal discharge rate and its implications for psychophysical performance. Nature, 370(6485), 140-143. https://www.nature.com/articles/370140a0", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Authors say: \\\"While one might expect the organized bands of spiking activity would result in increased correlations across neurons, we found no evidence that this was the case. The introduction of topographic connections\\\"\\n\\nThis seems to contradict the recent paper by Huang et al (Huang, Chengcheng, et al. \\\"Circuit models of low-dimensional shared variability in cortical networks.\\\" Neuron 101.2 (2019): 337-348) which showed a low dimensional shared variability both in experiments and in simulations. Do the authors have some idea why this differs from the present work? I believe their network was also sparsely connected as it was in the balanced regime and there were wavelike patterns seen as well.\\n\\nIt is hard to believe that there is no correlation for nearby neurons as a wave passes by or is it just that there was such a low probability of a given neurons being involved in the wave?\\n\\nHowever the difference between sparse and dense is interesting. The authors should plot the pairwise correlations of nearby neurons as a function of density of connection. I’d be interested in how this varies and at which point it is nonzero.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "\\\"sparsely modulated\\\"\\n\\nWhat does sparsely modulated mean?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Authors say:\\\"While previous computational models held that the contribution of axonal delays was negligible in their effects on the temporal properties of spiking networks,\\\"\\n\\nThere are a number of older papers that take distance dependent delays into consideration with regard to waves both in neural oscillations and waves. IN all of these the delays matter and lead to dynamics such as traveling waves among others. These should perhaps be discussed. Here is a list (not comprehensive)\\nCrook, Sharon M., et al. \\\"The role of axonal delay in the synchronization of networks of coupled cortical oscillators.\\\" Journal of computational neuroscience 4.2 (1997): 161-172.\\nAtay, Fatihcan M., and Axel Hutt. \\\"Neural fields with distributed transmission speeds and long-range feedback delays.\\\" SIAM Journal on Applied Dynamical Systems 5.4 (2006): 670-698.\\nGolomb, David, and G. Bard Ermentrout. \\\"Continuous and lurching traveling pulses in neuronal\\nnetworks with delay and spatially decaying connectivity.\\\" Proceedings of the National Academy of Sciences 96.23 (1999): 13480-13485.\\nGolomb, David, and G. Bard Ermentrout. \\\"Effects of delay on the type and velocity of travelling pulses in neuronal networks with spatially decaying connectivity.\\\" Network: Computation in Neural Systems 11.3 (2000): 221-246.\\nVenkov, N. A., Coombes, S., & Matthews, P. C. (2007). Dynamic instabilities in scalar neural field equations with space-dependent delays. Physica D: Nonlinear Phenomena, 232(1), 1-15.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Authors say: \\\"Spontaneous LFP fluctuations recorded simultaneously from a spatially distributed multielectrode array were structured as traveling waves\\\"\\n\\nI don’t see any traveling wave here. I see a transient increase in amplitude but nothing that looks like an actual moving wave. Am I missing something? Does the fact that the waves are \\\"traveling\\\" change the histogram shape in a way that would be different if these were just synchronized oscillations? That is, I see that the response is stronger at certain phases of the lfp, but I’d expect the same if no traveling was involved. I don’t see the role of the motion of the waves in the enhancement of the response. Indeed, it is hard to see how such motion could be relevant to a non moving stimulus. As an example of traveling waves having a computational role to a perception of a stimulus, see the recent paper of Heitmann and Ermentrout in PLoS Comp Bio 2020", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "The authors seem unaware of the work of the Doiron group on spatially balanced networks. See the recent paper with Huang ei al (op cit) fig 3 and 5 for examples of broad traveling waves. See also the papers with Rosenbaum and Doiron in PRX 2014 and Nature Neuroscience 2017\\n\\nHave you looked at a simpler one d system and the appropriate mean field spatial model?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "It may be that the reason that you need axonal delays to get the traveling waves is that you assumed that the spatial spread of excitation and inhibition were the same. As the paper does not specify in the parameter tables the time scales of the e and i synapses I could not say if this was also a reason. As seen in the Huang et al paper, it is easy to get wavelike activity without axonal delays when the spatial and temporal time scales are in the right ranges.\\n\\nI am puzzled by what is plotted in 3c. The network is two d and what is plotted is one d. Is this a slice or what is the spatial position denoting?\\n\\nIf the connectivity is random but there are distance dependent delays will the waves appear? If there is topological connectivity but no delays do the waves appear? I only saw simulations that had both features and I’d like to see which are necessary. That is, if the amplitude coupling is independent of distance but the delay does depend on distance matters more than if the delay is fixed and the amplitude varies with distance. It is known (say in the Crook et al paper above) that distance-dependent delays can destabilize the synchronous state. Is that what is happening here? This is why a mean-field and/or 1-dim network would be useful. It is not clear what the underlying mechanism is.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "7c is just reflecting your definition in which the LFP is just the difference between gi and ge so it should be strongly anticorellated. Am I missing some bigger point?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_1|9", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "In the LFP proxy, where do the values of the parameters come from? That is why is tau 6 and alpha 1.65?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_1|10", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "\\\"Ermentrout, G. B.\\\" is written twice", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Sparse waves are roughly defined by the authors as waves \\\"with only a small fraction of neurons spiking in any given wave\\\". This definition should be made mathematically precise by defining a measure that directly quantifies the notion of the \\\"fraction of neurons spiking in any given wave\\\". E.g one could compute the mean number of spikes \\\"per wave\\\" and neuron, maybe by computing the ratio of mean interspike interval to mean wave duration (at some local position). This direct measure should be applied to network simulations to convince the reader that the fraction of neurons spiking per wave is indeed much smaller than unity for the presumed sparse-wave network, whereas such a property would not hold for the presumed dense-wave network.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "As an indirect way to quantify sparse waves the authors consider the spike-spike coherence and argue that \\\"If it were the case that neurons strongly participated in these fluctuations, then they would show a degree of coherence in the range of frequencies dominated by those fluctuations.\\\" While I very much like this idea to use the coherence to characterize sparse waves, I have some concerns about the specific procedure used in the paper. The coherence is computed by picking 1000 random pairs of neurons from the whole extend of the network. Depending on the correlation length of neural activity, pairs of distant neurons could show very low spike-spike coherence and may thus lead to a small overall coherence and obscure local spike-spike coherence. Therefore, the authors should also show the local coherence computed across a local pool of neurons.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Apart from the overall magnitude of coherence, it is unclear whether dense vs. sparse wave regimes could also be distinguished by the presence or absence of a peak in the coherence at the peak frequency of the power spectrum. This difference is suggested by Fig.2i vs. Fig.S1b. In fact, for the dense network the maximal coherence is also quite low (~0.06), so the distinguishing feature seems to be the shape of the coherence. Please, clarify the conditions for sparse vs. dense waves more precisely in terms of the magnitude and shape of the coherence function.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Furthermore, the coherence of the full spike trains without eliminating spikes should be shown. Different rates are already accounted for by the normalization of the coherence. The deletion of spikes may introduce some artifacts or artificially reduce the coherence. Especially, I am worried that the deletion fixes spike counts, which completely removes possible effects of spike count variability on the spike-spike coherence. Please also add a mathematical definition of the spike-spike coherence.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Alongside with the coherence, please also show the power spectrum (which is contained in the denominator of the coherence function) in Fig 2. Does it have a band structure (as for the dense wave network in Fig.S1b) or does it lack a peak at a finite frequency (turbulent waves?)?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Another characterization of the sparse-wave regime relies on the comparison of firing rates, CV's and coherence with the corresponding statistics of a non-wave reference network: in the sparse-wave regime these statistics do not change. Although I find this comparison useful for the specific model, I guess it is not useful as a general condition for the sparse-wave regime because it is generally not obvious what would be a suitable reference model. Furthermore, a corresponding comparison of rates, CV's and coherence should also be shown for the dense-wave network and its corresponding random network.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Lines 401ff: The discussion on distance-dependent time delays in neural systems needs to be improved. There is extensive literature on the effect of delays on pattern formation, in general, and on traveling waves, in particular, see also the list of some important references at the end. Notably, the existence of traveling waves has been reported in neural fields with distance-dependent time delays, see, e.g., Atay, Hutt (SIAM, 2004), Venkow et al. (Physica D, 2007) and Veltz (SIAM, 2013), and also in spiking networks with fixed delay, see Roxin and co-workers (2005, 2006, 2011). Recently, traveling waves have also been analyzed in sparsely connected networks of LIF neurons with fixed delay (Senk et al., Physical Reviews Research 2020). It thus needs to be better worked out what the sparse-wave model of the manuscript at hand can add to the wealth of literature on the topic.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "The authors stress \\\"the importance of distance-dependent time delays\\\". While I understand that distance-dependence is biologically more realistic, it is unclear whether similar results can be achieved with fixed delays (either homogeneously or heterogeneously distributed across the network), see in particular Figure 1G in Kriener et al. (Front. Comput. Neurosci. 2013). Please discuss the distance-dependence of the delay.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Another important point is to report the main differences between the sparse-wave regime reported in Ref. 54 and the one studied here. It would be helpful to have a comparison with Ref. 54, e.g., with respect to whether the waves—arising due to different spatial connectivity ranges of excitation and inhibition and due to different membrane time scales \\( \\tau_{u_e} \\neq \\tau_{u_i} \\)—show similar spike-phase coupling to the LFP, and whether the effects of transient stimulations are comparable to the sparse-wave or dense-wave regimes studied in the manuscript at hand.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|10", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "The sparse wave regime reminds me of the phenomenon of sparse synchrony studied in Brunel & Hakim (Neural Comput. 1999) and Brunel & Wang (J Neurophysiol. 2003). It would be interesting to discuss possible differences and similarities of the mechanisms.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|11", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Relation between Fig.1A,B (corresponding to lines 99-117), which seems to serve as a motivation of the study, and the rest of the paper is unclear to me. In particular, I do not understand the sentence starting in line 119, and there are no simulations of the network model corresponding to Fig.1A,B.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|12", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "I am not convinced of the statement of Fig.1A,B \\\"Spontaneous network fluctuations are of similar magnitude to stimulus-evoked responses.\\\" (l. 464). The behavior in Fig.1A,B seems to be expected from the most naiv case, in which single trial fluctuations are composed of a stimulus-evoked component (corresponding to fluctuations of the trial-averaged mean LFP) and trial-by-trial variability (noise) equal to the amount of spontaneous fluctuations: For a weak stimulus the stimulus-evoked component becomes small, and thus only the noise remains leading to fluctuations of the same magnitude as the spontaneous fluctuations. In contrast, the fluctuations of the stimulus-evoked response (i.e. the trial-averaged response) is much smaller.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|13", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "l. 106, l. 468-469: is it 200ms or 100ms? There seems to be an inconsistency in different places of the paper.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|14", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Fig2i: Is coherence measured between only among E (or I) cells, or also between different cell types?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|15", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Line 157 and throughout the manuscript: There is no consistency in reporting micrometers either as \\\"\\mu m\\\" or as \\\"\\mu M\\\" or even \\\"uM\\\" (Fig.5a).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|16", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Line 222: how do you ensure that you are still in the balanced E/I regime?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|17", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Line 270: I suppose that the few long-range connections create a small-world topography. Is this correct? And if so, please provide proper references to the wide literature on small-world networks in neuroscience.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|18", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "How is the spike-phase coupling defined? Please add a definition.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|19", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Line 300,303: The authors ask: \\\"What is the conductance state [...] in the sparse-wave network simulation?\\\". They conclude a high (low) conductance state for sparse- (dense-) wave networks indirectly from the membrane potential distribution. This indirect argument is unclear. Why not measure and compare conductances explicitly for sparse- and dense-wave network simulations?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|20", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "l.317ff, Fig.7d: How is spike-phase coupling (spike-phase modulation) defined? Please add the mathematical definition. The z-scored numbers of the spike-phase coupling in Fig.7d are hard to interpret. Can you report the spike-phase coupling in its natural units, please?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|21", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "l. 325, 332, 336: please define \\\"circular-resultant\\\". Is it the length of the sample-mean circular resultant vector?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|22", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Line 322: \\\"(1 nS g_e, 10 nS g_i)\\\" -> (G_e = 1 nS, G_i = 10 nS)", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|23", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Line 335, Fig. S2: why does the random network exhibit a (weak) spike-phase coupling? Shouldn't the histogram be flat? Please, comment.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|24", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Line 419: \\\"Fig 4B\\\" -> Fig 4D ?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|25", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Line 671: g_{e,i} should have an additional neuron index as in line 679. Also, the subscript i is used for denoting both the index and the inhibitory cell type. Please use different symbols.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|26", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Line 678: is there also an absolute refractory period after resetting (in line with the experimental findings reported in line 633)?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|27", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Line 679: w_{e,i} are unused throughout the manuscript. I suppose they should read G_{e,i}, which are studied in Fig. 3 and reported in Tables S1,2. In the table, the units [S] are missing. Check also the inconsistency of these parameters in lines 763ff: G_e and G_i instead of g_e and g_i?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|28", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Line 679: How is the delay treated here? I think the rule in 679 only applies after a time delay.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|29", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Line 688: What are the explicit values of \\tau_{e,i} used in the simulations? Inhibition faster than excitation?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|30", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Line 692: How are the excitatory and inhibitory neurons arranged? Along a grid? Are excitatory and inhibitory neurons drawn randomly at each grid point or does the arrangement follow some proper rules? Please, describe the spatial arrangement of the neuronal network in more detail. Maybe provide a mathematical expression for the position of a given neuron j of type {e,i}.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|31", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Line 706: What is the physical motivation behind choosing periodic boundary conditions (except for mathematical convenience)? What is the influence of the boundary conditions on the wave patterns?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|32", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Line 701: what is the value of \\tau_s in the different simulations? This needs to be explained more carefully.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|33", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Line 743: \\\"Coherence was then computed [...], and normalized by the pooled power spectrum\\\". This sounds strange: by definition, the coherence contains already a normalization by the power spectra. Please provide a mathematical formula for the coherence.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|34", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Line 756: For reproducibility, please also add the Brian2 simulation code on the github page.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|35", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Line 786: What exactly is the value of m? I suspect m=80? Then the second sum should be from 1 to 20? Is it correct that in such a 10x10 pool, the synaptic input current involves the activity of around 300,000 neurons ( = 100neurons x 3,000synapses/neuron)?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|36", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Line 812: gradient \\\"approximated by the appropriate forward and centered finite differences\\\": Please provide explicit mathematical formulas for the computation of the gradient.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|37", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Line 813: \\\"phase derivatives were implemented as multiplications in the complex plane\\\". Please, provide formulas. Otherwise it is difficult to understand.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|38", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "line 816 \\\"Wave speed was computed as the ratio of instantaneous frequency to phase gradient magnitude\\\": how is the instantaneous frequency calculated?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|39", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Figure 1: a,b) How to interpret the plots on the right? In particular, what is the x-axis? What is relative power (is it relative variances?)? I guess the mean is not subtracted when computing variances over time, right? Please provide formulas!\\nc) why a 9x9 grid?\\nd) at which point in space is the LFP computed? Is it an average over the 10x10 neuron pool, or does it correspond to the LFP at the center neuron of this pool?\\ne) It needs to be made more explicit what aligned vs unaligned means.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|40", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Figure 2: how to interpret the raster plots? Is a particular coordinate fixed, say y = y_0, and then the y-axis of the raster plot corresponds to the x-coordinate of the plane?\\nIs the mean rate the mean of all neurons or only of the excitatory ones?\\nWhy are mean rate and LFP z-scored?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|41", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Figure 4: a) Which quantity is exactly plotted here? Please provide mathematical definition of \\\"Fraction of Wave State\\\"! I guess it is the vertical distance between the blue and the red curve at the dashed line in Fig.3d, right?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_2|42", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "Figure S1: there is no panel c).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|25|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb25", "comment": "However, my major concern with this paper is the strong assumption (given strong evidence to the contrary) that intrinsically generated asynchronous-irregular states are a dominant mode of cortex during wakefulness and that they could explain traveling waves.\\nSpecifically, the authors should reconcile their findings in the context of two strong experimental results that show that cortex becomes quite silent (within ~10 ms) when thalamus is inactivated:\\nGuo et al., 2017. Nature Vol 545, p181\\nReinhold et al., 2015. Nature Neuroscience. Vol 18. No 12.\\n\\nBoth of these papers provide strong evidence that refutes the hypothesis that cortical activity is intrinsically driven in a sustained manner by such AI dynamics.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|Claude|1", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "The paper's validation of the EZN estimation pipeline is performed entirely on synthetic data generated by the same generative model (Epileptor-Stimulation) that underlies the inference procedure, creating a methodologically circular validation that cannot demonstrate real-world clinical utility.\n\n\"This framework estimates the EZN and validated the results on synthetic data with ground-truth.\"\nThe paper explicitly acknowledges that validation is only performed on synthetic data. This is problematic because when the same model generates both the training/testing data and performs the inference, the results are tautologically guaranteed to be consistent. The Epileptor-Stimulation model generates seizure dynamics with known parameters (including the EZN), and then a reduced 2D Epileptor model is used for inference. Since both share the same fundamental dynamics, recovering the ground-truth parameters is expected rather than a validation of clinical utility.\n\"As the ground truth is known for the simulated data, we can formally validate the EZN estimation.\"\nWhile knowing the ground truth is valuable, the critical limitation is that the synthetic data was generated by the same modeling framework used for inference. This creates an idealized scenario that does not test the model's ability to handle the variability, noise characteristics, and complexity of real SEEG/EEG recordings from actual stimulation-induced seizures. A more rigorous validation would require comparison against empirical data where the EZN has been independently confirmed through surgical outcome.\n\"Our personalized whole brain model has the ability to predict the stimulation effect for individual patients given specified stimulation parameters and should be validated in future empirical studies.\"\nThe paper itself acknowledges that empirical validation is needed in future studies. This is a significant gap because the current claims about the pipeline's clinical applicability rest entirely on simulated scenarios. Recent work on virtual epileptic patient cohorts, such as the EBRAINS Virtual Epileptic Cohort, demonstrates that proper validation requires comparing synthetic data against real intracranial recordings and surgical outcomes to confirm patient-specific EZ identification [[1]](#ref1).\n\"We ran the model inversion on both empirical and simulated seizures with 16 chains starting from eight optimized initial conditions.\"\nAlthough the paper mentions running model inversion on \"empirical\" seizures, the actual results presented in Figures 3-7 for stimulation-induced seizures are all based on simulated data. The only empirical data used (spontaneous seizures in Fig. 2) serves only to establish the EZ hypothesis, not to validate the stimulation-based estimation pipeline.\n\nReferences:\n[1] [EBRAINS: Thirty New Personalised 'Virtual Brain Twins' Offer Ground Truth for Epilepsy](https://ebrains.eu/news-and-events/2025/thirty-new-personalised-virtual-brain-twins-offer-ground-truth-for-epilepsy)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|Claude|2", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "The paper proposes TI stimulation as a future approach for non-invasive EZN diagnosis through seizure induction, but no empirical evidence exists demonstrating that TI can safely or reliably induce seizures in human epilepsy patients, making this a purely theoretical proposition rather than a validated clinical approach.\n\n\"We consider invasive SEEG stimulation as the most practical current approach, and temporal interference (TI) stimulation as a potential future approach for non-invasive diagnosis and treatment.\"\nWhile TI is described as a \"potential future approach,\" the paper treats it as an equivalent alternative to SEEG stimulation in the methodology without acknowledging that TI has never been used to induce seizures in humans for diagnostic purposes. The original Grossman et al. (2017) study demonstrated TI in mice for motor cortex stimulation, not seizure induction in epilepsy [[2]](#ref2).\n\"TI stimulation has evoked seizure-like events in the mouse hippocampus that have been experimentally well controlled [40].\"\nThe cited reference (Missey et al.) demonstrates TI effects in mice, not humans. More recent human studies on TI, such as Violante et al. (2023), have demonstrated hippocampal modulation for memory enhancement in healthy humans, but not seizure induction [[3]](#ref3). The translational gap from controlled mouse experiments to human epilepsy patients seeking diagnosis through intentional seizure induction is substantial and requires safety and efficacy data that does not exist.\n\"The diagnostic pipeline for TI stimulation can provide a theoretical basis for non-invasive diagnosis and treatment of epilepsy.\"\nThe claim of providing a \"theoretical basis\" for TI-based diagnosis is valid, but the paper conflates theoretical modeling with clinical validation. Recent reviews on TI stimulation progress emphasize that while TI shows promise for neuromodulation, its clinical applications require \"careful evaluation on TI's safety and ethical considerations\" and that \"long-term stimulation effects, measures for individual differences, and potential side effects still need systematic evaluation\" [[4]](#ref4).\n\"Studies have demonstrated the safety of TI in human participants [35].\"\nThe cited safety studies refer to TI for cognitive enhancement (working memory) in healthy participants using low-intensity stimulation parameters, not high-intensity stimulation designed to provoke seizures in patients with epilepsy. Using TI to intentionally trigger seizures for diagnostic purposes raises fundamentally different safety concerns that have not been addressed empirically.\n\nReferences:\n[2] [Grossman N, et al. Noninvasive deep brain stimulation via temporally interfering electric fields. Cell. 2017;169(6):1029-1041](https://doi.org/10.1016/j.cell.2017.05.024)\n[3] [Violante IR, et al. Non-invasive temporal interference electrical stimulation of the human hippocampus. Nature Neuroscience. 2023;26(11):1994-2004](https://www.nature.com/articles/s41593-023-01456-8)\n[4] [Progresses on temporal interference electromagnetic stimulation for deep brain function modulation. PMC. 2025](https://pmc.ncbi.nlm.nih.gov/articles/PMC12744965/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|Claude|3", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "The validation of the virtual brain twin pipeline for stimulation-based EZN estimation is demonstrated on only two patients (one with occipital lobe epilepsy and one with frontal lobe epilepsy), which is insufficient to establish the generalizability and reliability of the approach across different epilepsy types and patient anatomies.\n\n\"We used the data from a right-handed 23 years old female patient diagnosed with left occipital lobe epilepsy to illustrate how to use our workflow.\"\nThe primary patient is described as an illustration rather than a systematic validation case. With only a single patient for the main demonstration and one additional patient for \"validation,\" the paper cannot establish whether the pipeline generalizes across the heterogeneous population of drug-resistant epilepsy patients.\n\"To validate that the pipeline can be easily used in other patients, we added the results of a second patient with left frontal lobe epilepsy.\"\nAdding only one additional patient does not constitute meaningful validation. The prior VEP workflow referenced by the authors was \"evaluated retrospectively using 53 patients with 187 spontaneous seizures\" and is being evaluated in the EPINOV clinical trial with \"an expected 356 prospective patients.\" In contrast, demonstrating the stimulation pipeline on only 2 patients represents a dramatic reduction in validation scope that limits confidence in the generalizability of the results.\n\"The patient underwent resective surgery resulting in seizure freedom (surgery outcome class of Engel I [27]).\"\nWhile surgical outcome provides some external validation, the pipeline is tested only on patients where the hypothesized EZ (left O2 for Patient 1, left F1-lateral-prefrontal for Patient 2) was already established. Both patients had successful surgeries, representing best-case scenarios. The pipeline is not tested on patients with failed surgeries, multifocal epilepsy, or uncertain EZ localization—precisely the cases where such a tool would be most clinically valuable.\n\n* Quote from literature: \"Small sample sizes in neuroscience have historically been small, producing low statistical power and inflated\" effect sizes [[5]](#ref5).\nThe neuroscience literature has extensively documented problems with small sample validation studies. With only two patients, there is no ability to assess reproducibility, inter-patient variability, or statistical reliability of the EZN estimation procedure.\n\nReferences:\n[5] [Translating EEG Biomarkers into Clinical Tools. PMC. 2025](https://pmc.ncbi.nlm.nih.gov/articles/PMC12724633/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|Claude|4", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "The paper assumes that the EZN estimated from stimulation-induced seizures will match the EZN of spontaneous seizures, but this fundamental assumption is acknowledged as unvalidated and may not hold in clinical practice.\n\n\"Second, what is the relationship between the EZN triggered by stimulation and the one occurring during spontaneous seizures? More specifically, we want to investigate whether the EZN estimated from stimulation induced seizures equals the EZN of spontaneous seizures.\"\nThe paper explicitly frames this as an open research question that needs to be investigated, yet the entire pipeline is built on the implicit assumption that stimulation-induced seizures will reveal the same EZN. Without validating this assumption, the clinical utility of the approach remains uncertain.\n\"It could be possible that stimulation forces seizures in brain regions that would not be epileptogenic otherwise, or that stimulation uncovers only a subset of epileptogenic regions.\"\nThe paper acknowledges two critical failure modes: (1) stimulation could trigger seizures in non-epileptogenic regions (false positives), and (2) stimulation might only reveal a subset of epileptogenic regions (false negatives). Both scenarios would lead to incorrect EZN estimation, yet no empirical data or simulation studies are presented to quantify these risks.\n\"Based on this result, we built the high-resolution whole brain model for SEEG- and TI-stimulation with the hypothesis that the left O2 was the EZ of the patient.\"\nThe methodology is circular: the EZ identified from spontaneous seizures (left O2) is used as the ground truth for the stimulation simulations. This design cannot test whether stimulation-induced seizures would identify the same EZ if it were unknown. A proper validation would require blind estimation from stimulation-induced seizures followed by comparison with independently confirmed EZ.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|Claude|5", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "For the second patient, the TI stimulation-based EZN estimation identifies a different primary region (left-middle-frontal-sulcus) than what was hypothesized and surgically resected (left-F1-lateral-prefrontal), but this discrepancy is not adequately addressed or explained.\n\n\"We obtained the left-F1-lateral-prefrontal cortex as the region with the highest EV from the HMC algorithm (Fig. 6D,E).\"\nUnder SEEG stimulation, the pipeline correctly identifies left-F1-lateral-prefrontal as the primary EZN candidate, consistent with the surgical resection that led to seizure freedom.\n\"We obtained the left middle frontal cortex as the region with highest EVs from all samples (Fig. 7D)\"\nUnder TI stimulation for the same patient, the primary EZN candidate shifts to left-middle-frontal-sulcus, which is different from the SEEG stimulation result and the surgical resection outcome. This inconsistency is concerning because both methods should theoretically identify the same EZN if the patient's underlying epileptogenic network is stable.\n\"Fig. 7 ... (E) The highest chance of being the EZN as left-middle-frontal-sulcus in red mapped in 3D brain and left-F1-lateral-prefrontal and left-orbito-frontal-cortex in yellow.\"\nThe paper does not discuss why TI and SEEG stimulation yield different primary EZN candidates for the same patient. This discrepancy could reflect (1) limitations of TI to target the true EZ, (2) sensitivity to stimulation parameters, or (3) inherent variability in the estimation procedure. Without quantitative uncertainty analysis or explanation, readers cannot assess which result is more reliable or whether either should be trusted clinically.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|GPT|1", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "This paper’s central evidence for accurate EZN inference under stimulation is not a valid validation because the “ground-truth” EZN is assumed when generating synthetic stimulation-induced seizures and then re-identified from those same synthetic signals, rather than being independently established from real stimulation-induced seizure data.\n\n\"This framework estimates the EZN and validated the results on synthetic data with ground-truth.\"\nThis sentence makes the paper’s strongest validation claim hinge on synthetic data, which is inherently weaker than validation on empirical stimulation-induced seizures. In model-based inference, using synthetic data is useful for debugging but does not by itself establish that the inversion will work on real recordings where model mismatch, noise, and unmodeled physiology dominate. The paper does not specify an external ground truth for stimulation-induced seizures (e.g., stimulation-evoked seizure recordings with independent clinical localization). As written, the “ground-truth” is not tied to an independent measurement of the stimulated-seizure EZN. This creates a high risk that the reported recovery is primarily a self-consistency check of the authors’ generative assumptions.\n\"Based on this result, we built the high-resolution whole brain model for SEEG- and TI-stimulation with the hypothesis that the left O2 was the EZ of the patient.\"\nHere the paper explicitly states that a hypothesized EZ (left O2) is assumed when constructing the stimulation simulation. That means the subsequent stimulation-induced seizure simulations are conditioned on an assumed EZN configuration, rather than deriving it from stimulation data. If the EZN is baked into the simulation setup, then recovering it from the synthetic data is not an independent test of the method’s diagnostic capability. A robust validation would vary unknown EZN configurations and show reliable recovery across many held-out scenarios, ideally with realistic noise and forward-model errors. At minimum, the paper should quantify how often the inversion fails or confuses nearby regions under perturbations of the assumed EZ.\n\"These synthetic SEEG recordings (Fig. 3C) were used for model inversion, to estimate the EZN.\"\nThis sentence confirms that the headline stimulation results are based on synthetic sensor data rather than empirical stimulation-induced seizures. Because the same modeling pipeline defines both the forward simulation and the inverse model, the experiment risks “inverse crime” behavior where inversion succeeds largely because the data are generated from the same model family. This is a major threat to validity in computational neuroengineering, where real data commonly violate modeling assumptions (conductivity, electrode contact effects, nonstationary dynamics, stimulation artifacts). Without reporting robustness to model misspecification (e.g., wrong conductivities, wrong coupling, wrong stimulation-to-neural coupling), it is not possible to conclude the inversion will work clinically. The result therefore does not yet justify the paper’s claims of a practical diagnostic workflow for stimulation-induced seizures.\n```python\nlocal_con_scaling = 0.9\nglobal_con_scaling = 0.1\nEZ = 'Left-F1-lateral-prefrontal'\n```\nThis code (from the provided example notebook) sets an explicit EZ label before simulation, indicating that the “ground-truth” EZN is user-specified rather than unknown. That is consistent with the manuscript’s repeated phrasing “under the hypothesis that … is the EZ,” and it undermines any claim that the pipeline objectively discovers the EZN from stimulation data in these demonstrations. A validation that fixes the answer in the code and then re-identifies it from synthetic outputs cannot establish diagnostic accuracy. Instead, it mainly shows that the pipeline can recover an imposed configuration given idealized generative conditions. The paper should separate (i) simulation configuration, (ii) inversion target, and (iii) independent evaluation to avoid circular confirmation.\n```python\nepileptors.x0 = np.ones((n_nodes)) * (-3.5)\nepileptors.threshold = np.ones((n_nodes)) * (100.0)\n...\nepileptors.x0[idx_vertices] = -2.2  # setting this region close to criticality\nepileptors.threshold[idx_vertices] = 1.8\n```\nThis code explicitly forces the chosen EZ region toward ictogenicity (“close to criticality”) and lowers its threshold, which directly shapes where seizures emerge in the simulation. Because the inversion is then evaluated on data generated from this setup, the method is effectively asked to rediscover a parameter configuration that was imposed upstream. This is not equivalent to identifying an EZN from real stimulation-induced seizures where the true parameter heterogeneity is unknown and may not be well-approximated by such a construction. The paper does not show that alternative plausible parameterizations (e.g., distributed excitability changes, multiple competing foci) would still be correctly inferred. As a result, the main conclusion about validated stimulation-based EZN diagnosis is not adequately supported.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|GPT|2", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "The manuscript over-claims that TI stimulation is “focal” and can non-invasively stimulate deep structures for EZN diagnosis, but its TI implementation projects fields onto the cortical surface and relies on simplified assumptions that conflict with published analyses indicating key mechanistic uncertainties and weak human-scale field strengths.\n\n\"Thus combining the advantages of tDCS and DBS [23], TI stimulation [24] is both non-invasive and focal and can stimulate deep structures of the brain.\"\nThis is a strong mechanistic and practical claim that TI is both focal and capable of stimulating deep structures. Such a claim requires careful qualification because “deep” and “focal” depend on achievable field magnitudes, off-target stimulation, and the biophysical mechanism by which neurons respond to kHz carriers. The paper does not present empirical human evidence of deep EZN diagnosis with TI, nor does it quantify whether the simulated fields reach neuronal activation thresholds in deep targets. In computational studies, reporting field strength alone is not sufficient without translating it into expected neural effects and safety-limited currents. Without these links, the statement risks misleading readers about TI’s readiness for clinical translation.\n\"We calculated the TI electric field, which is projected onto the cortical surface by stimulating two pairs of scalp-EEG electrodes …\"\nThis sentence indicates that the TI field used to drive the brain model is explicitly projected onto the cortical surface. That choice is inconsistent with the manuscript’s repeated emphasis on TI’s ability to stimulate “deep structures,” because a cortex-projected drive cannot represent direct modulation of deep nuclei such as hippocampus. Moreover, epilepsy EZNs often involve mesial temporal structures where deep targeting is precisely the challenge; a cortex-only stimulation drive would miss that mechanism. If the method’s claimed advantage is deep focusing, then the model should include deep-field coupling and evaluate sensitivity when the EZN is subcortical or mesial. As implemented, the TI results primarily demonstrate cortex-level stimulation effects, so conclusions about deep EZN diagnosis are not justified.\n\"The key feature of TI stimulation is that it enables a focused stimulation which can reach deep brain structures non-invasively [24, 34], such as the hippocampus …\"\nThis discussion asserts deep, focused stimulation as a key feature motivating the proposed non-invasive diagnostic pipeline. However, the paper does not demonstrate hippocampal or other deep-structure EZN localization using TI-driven scalp-EEG in a way that is independently validated. The authors also note difficulty with deep structures elsewhere, but the pipeline is still presented as a “necessary step” for non-invasive diagnosis. The burden of proof is especially high because deep stimulation via TI in humans remains an active research question rather than an established clinical capability. Without aligning the modeling assumptions to current mechanistic understanding and showing realistic deep-target effects, this claim is not sufficiently supported.\n\"We argue that TI stimulation cannot work via passive membrane filtering, as previously hypothesized. Instead, TI stimulation requires an ion-channel mediated signal rectification process.\" ([2](#ref2))\nThe manuscript’s TI description emphasizes tissue “insensitivity” above 500 Hz and implicitly treats the low-frequency envelope as an effective stimulation, which aligns with a passive-filtering intuition. Mirzakhalili et al. explicitly argue that passive membrane filtering cannot explain TI and that a nonlinear rectification mechanism is required, which is a materially different biophysical picture. If the mechanism is rectification and is tied to high-frequency conduction block in off-target tissues, then translating TI to safe, focal, deep stimulation in humans is more constrained than the manuscript suggests. The paper’s modeling does not appear to include ion-channel rectification or the off-target conduction-block constraints, so it may not capture the relevant operating regime. This discrepancy directly undermines the validity of claims about TI-based clinical diagnosis.\n\"Maximum field strengths in the human model were much lower than in the murine model, too low to expect direct stimulation effects.\" ([1](#ref1))\nThe manuscript uses TI stimulation to induce seizures in simulations and then infer the EZN from the resulting synthetic scalp-EEG. Rampersad et al. report that, at human scale, maximum TI field strengths are much lower than in mice and may be too low for direct stimulation, highlighting a fundamental feasibility constraint. If direct stimulation is unlikely at safe currents, then seizure induction and robust diagnostic modulation become questionable without a clear alternative (e.g., subtle entrainment rather than seizure triggering). The paper does not quantify whether its simulated TI fields fall into a regime expected to modulate neural dynamics in humans. Therefore, the conclusion that TI provides a practical basis for non-invasive EZN diagnosis is not robust.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|GPT|3", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "The manuscript’s “Data, Materials and Software Availability” statement is too vague and conflicts with the extensive external dependencies and upstream pipelines required to reproduce the personalized high-resolution models, electric-field computations, and Bayesian inference results.\n\n\". All shareable codes and data are included in the manuscript and/or Supplementary documents.\"\nThis statement implies that a reader can reproduce the work using only the provided materials. However, the core workflow depends on patient-specific MRI/CT/DWI processing, tractography, electrode localization, and field modeling, which are not fully contained in the manuscript text itself. Even if raw patient data cannot be shared, reproducibility requires either (i) a complete, runnable pipeline with representative example data and expected outputs, or (ii) shareable derived artifacts sufficient to regenerate the figures and results. The paper does not specify what exactly is provided versus what is restricted, nor does it provide a clear provenance trail from raw data to final results. This materially limits independent verification of the claims.\n\"Dependencies:\" (followed by) \"• FreeSurfer 6. 3.0…\"; \"• Mrtrix 0.3.16…\"; \"• SIMNIBS 4.0…\"; \"• Brainstorm3…\"; \"• Stan v.2.21.0…\"\nThe provided code explicitly requires a long chain of specialized neuroimaging and modeling tools across different ecosystems (FreeSurfer, MRtrix, SimNIBS, Brainstorm, Stan, etc.). In computational neuroscience, such multi-tool workflows are reproducible only when versioning, installation, and invocation details are fully specified (often via containers or workflow managers), because small version changes can alter surfaces, connectomes, or fields. The paper does not provide an executable environment definition (e.g., Docker/Singularity image) in the manuscript materials. As a result, even with the Python code present, reproducing the end-to-end pipeline is unlikely for external groups. This undermines methodological transparency and the credibility of “ready for clinical translation” implications.\n\"Structural scaffold reconstruction: https://github.com/ins-amu/tvb-pipeline\"\nThis shows that a critical upstream component of the pipeline is delegated to a separate repository rather than being fully contained in the provided package. That is not inherently wrong, but it means reproducibility depends on synchronizing multiple codebases and their dependencies. The manuscript does not pin versions/commits of the external pipeline nor describe how its outputs map into the stimulation workflow’s expected inputs. In practice, such unpinned external dependencies are a common source of irreproducible results. A reproducible paper would specify exact versions and provide a scripted “one command” pathway to regenerate key figures from a provided dataset.\n\"Basic usage requires invoked `make` with a subject name and your dataset\" and \"`conn`: Connectivity matrices in text format. Uses `T1` and `DWI`.\" ([4](#ref4))\nThe external pipeline explicitly requires access to subject-specific T1 and diffusion MRI data to generate connectivity and surfaces, and this is essential to the paper’s “personalized” modeling claim. The current repository only contains some spreadsheets and simulation outputs, not the full imaging datasets needed to rerun these steps. Without at least one fully shareable example subject (or an openly licensed benchmark dataset with a complete reproduction script), independent readers cannot validate the structural scaffold reconstruction or confirm that downstream inference behaves as reported. This breaks the chain of reproducibility from raw inputs to inferred EZN. Given that personalization is central to the paper’s contribution, the inability to reproduce personalization steps is a major methodological gap.\n\"CmdStanPy … wraps the CmdStan command line interface\" ([3](#ref3))\nThe Python project depends on `cmdstanpy`, which in turn requires a functioning CmdStan toolchain (compiler toolchain, model compilation, and runtime environment). This is a known friction point for reproducibility because the compiled model binaries, compiler versions, and platform differences can affect whether sampling runs at all. The paper and code do not provide precompiled models, pinned CmdStan versions, or a containerized setup that guarantees successful compilation and sampling. For Bayesian inference pipelines, inability to reproduce sampling is not a minor inconvenience—it prevents verification of posterior results entirely. This further contradicts the paper’s implication that materials are readily sufficient.\n\"All scholarly digital research objects—from data to analytical pipelines—benefit from application of these principles, since all components of the research process must be available to ensure transparency, reproducibility, and reusability.\" ([5](#ref5))\nThe FAIR principles emphasize that reproducibility requires availability of the full research object chain, including workflows and pipelines, not just partial code. The manuscript’s workflow spans MRI processing, tractography, electrode localization, field modeling, forward modeling, and HMC inference, yet the provided materials do not establish that an external group can rerun these steps end-to-end. The gap is especially important here because small differences in any upstream component can materially change downstream EV posteriors. The paper’s data/software availability claim therefore falls short of widely endorsed community expectations for computational research artifacts. This is a significant barrier to independent replication and practical adoption.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|GPT|4", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "The manuscript’s multimodal inference narrative includes a case where SEEG and scalp-EEG data are not simultaneously recorded and the validity is asserted to depend on HMC covering all feasible initial conditions, but the paper does not demonstrate that this assumption holds, threatening the reliability of the integrated EZN estimates.\n\n\"Notice that, in this case, the functional SEEG and scalp-EEG data here were not simultaneous recorded. The SEEG and TI stimulation generated the seizures with different initial conditions. Then results would be valid only with an assumption that the HMC sampled all feasible initial conditions.\"\nThis passage directly acknowledges that one multimodal integration scenario is only conditionally valid under a strong assumption about the sampling covering all initial conditions. In seizure models with multistability and strong sensitivity to initial conditions, this is a nontrivial requirement and cannot be taken for granted. The paper does not provide empirical or quantitative evidence that the sampler actually integrates over the relevant initial-condition uncertainty in this non-simultaneous setting. Without such evidence, pooling posteriors across modalities with different initial conditions can produce misleading “consensus” EZNs that reflect sampling artifacts rather than true multimodal agreement. Because multimodal integration is presented as a key advantage for clinical decision making, this unvalidated assumption materially weakens the conclusion.\n\"We assessed model identifiability based on an analysis of posterior samples, which demonstrated that the sampler explores all the modes in the parameter space efficiently. The analysis includes trace-plots … pair plots … and autocorrelation plots …\"\nThe paper’s stated identifiability assessment is based on standard MCMC diagnostics, but these do not by themselves guarantee that all clinically relevant initial conditions or latent states have been adequately marginalized in a complex dynamical system. Trace plots and effective sample sizes can look reasonable even when the sampler fails to explore rare but important modes, especially if the posterior is high-dimensional and multimodal. The paper also describes starting from a finite set of optimized initial conditions, which further suggests the exploration is constrained rather than exhaustive. Therefore, using this identifiability check as justification for cross-modality pooling under different initial conditions is not sufficient. This undermines confidence in the multimodal inference results beyond the idealized simultaneous case.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "The paper fails to validate the proposed framework using real stimulation-induced seizure data from the patients, despite such data likely being available or essential for a clinical diagnostic claim.\n\n\"We simulate the brain responses induced by SEEG stimulation and estimate the EZN based on the induced seizures. As the ground truth is known for the simulated data, we can formally validate the EZN estimation.\"\nThe authors explicitly state that they validate their EZN estimation on *simulated* data where the \"ground truth\" is known (because they put it there). This is a circular validation. For a clinical diagnostic framework, the crucial test is whether the model can predict the *actual* EZN or the *actual* response to stimulation in a real patient.\n\"These synthetic SEEG recordings (Fig. 3C) were used for model inversion, to estimate the EZN.\"\nThe use of synthetic recordings for inversion confirms that the framework's ability to handle real-world noise, artifacts, and complex biological dynamics (not captured by the model) remains untested.\n\"SEEG stimulation... is an important tool for localizing the EZ and are also associated with a better post-surgical outcome [18–20].\"\nThe authors acknowledge that SEEG stimulation is a standard clinical tool. Since they had access to the patient's SEEG data (used for spontaneous seizures), the omission of validation against the patient's *actual* stimulation-induced seizures is a significant methodological gap. Validating that the \"Virtual Brain Twin\" behaves like the real brain under stimulation is a prerequisite for using it for diagnosis.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "The validation strategy suffers from an \"inverse crime,\" where the same mathematical model (the Epileptor) is used for both generating the synthetic data and inverting it to estimate parameters.\n\n\"We simulated the time series on the patient’s specific structural scaffold using the phenomenological Epiletor model [25]... Model inversion estimates patient-specific brain model parameters... based on the structural brain scaffold, modelled seizure dynamics...\"\nThe authors use the Epileptor model to generate the \"ground truth\" data and then use a Bayesian inversion framework based on the *same* Epileptor dynamics to recover the parameters. This guarantees a high degree of model-data match that does not exist in reality.\n\"We used the Epileptor-Stimulation model on each of the 20,284 vertices... From these simulated neural source signals... we obtained SEEG signals... These synthetic SEEG recordings... were used for model inversion\"\nWhile the generation is high-resolution (vertices) and the inversion is likely lower-dimensional (regions), the underlying generative equations are identical. This \"inverse crime\" [1] leads to overly optimistic performance estimates because it ignores model specification errors—the inevitable discrepancy between the mathematical model and the complex biological reality of the human brain.\n\"As the ground truth is known for the simulated data, we can formally validate the EZN estimation.\"\nThis statement misinterprets the nature of validation. Recovering parameters from data generated by the same model validates the *inversion algorithm's* consistency, but it does not validate the *model's* physiological accuracy or clinical utility.\n\nReferences:\n[1] Kaipio, J., & Somersalo, E. (2005). Statistical and computational inverse problems. Springer Science & Business Media. https://link.springer.com/book/10.1007/b138659", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "The paper presents Temporal Interference (TI) stimulation as a viable component of the diagnostic framework based solely on simulations, without providing experimental evidence that TI can reliably induce seizures in the modeled specific brain regions.\n\n\"We consider... temporal interference (TI) stimulation as a potential future approach for non-invasive diagnosis and treatment. This paper offers a virtual brain twin framework for EZN diagnosis based on stimulation-induced seizures.\"\nThe authors frame the paper as offering a framework for diagnosis, implying a level of readiness or validity. However, TI stimulation is still an emerging technology with ongoing debates about its efficacy and mechanism in humans [2].\n\"For the TI stimulation, we calculated the envelope amplitude of the TI electric field for each vertex... Both types of stimulation generated an accumulative increase in the state variable m of the Epileptor-Stimulation model\"\nThe authors *assume* a specific mechanism (accumulation of variable $m$ proportional to the TI envelope) without citing experimental validation for this specific interaction between TI fields and epileptogenic tissue. If this assumption is incorrect, the entire TI section of the framework is invalid.\n\"We demonstrate now how the pipeline works on TI stimulation... We simulated the brain source signals... We then mapped the activities... onto the scalp-EEG signals... We extracted the data features... as input to the HMC model inversion\"\nThe entire TI \"demonstration\" is a simulation based on unvalidated assumptions. Presenting this as a \"result\" (Section 2.3) rather than a theoretical exploration is misleading regarding the maturity of the method.\n\nReferences:\n[2] Grossman, N., Bono, D., Dedic, N., Kodandaramaiah, S. B., Rudenko, A., Suk, H. J., ... & Boyden, E. S. (2017). Noninvasive deep brain stimulation via temporally interfering electric fields. Cell, 169(6), 1029-1041. https://www.cell.com/cell/fulltext/S0092-8674(17)30584-6", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "The assumption of homogeneous local connections across the cortex is a significant simplification that may compromise the model's ability to accurately localize the Epileptogenic Zone (EZ), which is often characterized by local structural and functional abnormalities.\n\n\"Although local connections are actually heterogeneous with a complex variability of interneurons and dendritic arborization, due to lack of personalized measurement in clinical routines, we made an assumption of homogeneity in the local connections\"\nThe authors explicitly acknowledge that local connections are heterogeneous but assume homogeneity for the model. In epilepsy, local microcircuit alterations (e.g., in Focal Cortical Dysplasia) are often the *cause* of the EZ.\n\"The default parameters of the system are... \\(\\gamma_{hom} = 0.8\\)...\"\nBy fixing local connectivity parameters globally, the model forces all regional differences to be explained by the \"excitability\" parameter ($x_0$) or long-range connectivity. This could lead to misattribution of epileptogenicity, especially if the true EZ is driven by abnormal local connectivity rather than just excitability.\n\"The model inversion uses a noninformative prior where all the brain regions have the same prior distribution (the prior assumption is that all regions are healthy).\"\nCombining the homogeneity assumption with a uniform prior might bias the model against detecting EZs that rely on local structural deviations not captured by the DTI-derived connectome (which only captures long-range fibers).", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|Gemini|5", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "The paper claims to establish a general \"framework\" for EZN diagnosis but demonstrates it in detail on only a single patient case (with a second mentioned in supplementary), which is insufficient to establish robustness or generalizability.\n\n\"We used the data from a right-handed 23 years old female patient diagnosed with left occipital lobe epilepsy to illustrate how to use our workflow.\"\nThe main text results focus almost exclusively on this single patient (Patient 1).\n\"We used the data from two patients who underwent a standard presurgical protocol\"\nAlthough the methods mention two patients, the results and detailed analysis (Figures 2-4) are presented for only one.\n\"This paper offers a virtual brain twin framework for EZN diagnosis... validated the results on synthetic data\"\nA \"framework\" implies a systematic approach applicable to a population. Demonstrating it on N=1 (or N=2) synthetic cases is a proof-of-concept at best, not a validated framework. The variability in epilepsy etiologies and brain structures requires a larger cohort to demonstrate that the pipeline is robust.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "Activity is simulated at each vertex (20284), however heterogenous coupling is only used for connections between regions in the VEP parcelation (162). The local coupling is distance dependent and is scaled by a factor yhom which is invariant across ROIs. Considering that increased connectivity within the EZ is observed in focal epilepsy, homogenous local coupling may be a strong assumption.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "The site of stimulation used in the virtual pipeline was determined based on the regions resected during surgery, and appears to be proximal to the previously identified EZ. It is possible that the model is producing type 1 errors by identifying most stimulated regions as epileptogenic. To rule out this possibility, I suggest delivering the same stimulus to an unrelated part of the cortex, and observing if the model still identifies it as an EZ.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "Can the epileptor model parameters be accurately estimated from surface EEG alone? If so, this method coupled with Temporal Interference could provide an entirely non-invasive treatment for drug resistant epilepsy.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "Allowing y_hom to vary across ROIs and determining its values for each participant could add another dimension to the subject specificity of the treatment and improve the method’s accuracy.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "Figure 1: The plots within sub figures B, E, F have axis labels and ticks that are illegible at this scale and create visual clutter.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "Line 114; Local and global propagation of seizures across vertices is mentioned separately, ostensibly because the local propagation occurs under homogeneous coupling. However, since that distinction is only made later in the article the phrasing here seems awkward.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "Line 161; Consider replacing “with the hypothesis” with “to test the hypothesis”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "Figure 7: In the caption, the heading for subfigure E is not bold, as the other headings are.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "In the data processing step to construct individual brain network models, the authors used parcellation of the cortex using a VEP atlas. Are there any limitations in using other atlas for the individual connectome construction?\\n\\nIt is perhaps not clear what the scientific rationales are for choosing the VEP atlas for the individual connectome of the patients over other existing atlases.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "VEP atlas is derived from their previous study the code/script and reference are included. However, I feel some more details should be provided in this manuscript to aid the readers in understanding the implemented pipeline.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "Are the results of the stimulation sensitive to the choice of the VEP atlas and location of the brain regions determined by the atlas, or is it generalizable and the stimulation results based on SEEG/Scalp EEG data are reproducible regardless of the choice of this atlas to construct virtual brain twins? Perhaps the authors can explain this in more detail.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "The authors mentioned that exposure to repetitive stimulation/perturbation generates a slow accumulation effect, which can push the system to the seizure state when a seizure threshold is reached. Beyond this excitability threshold, a network of neurons likely exhibits a high firing rate and increase in spiking activity.\\n\\nThe authors use this logic to introduce a slow variable that mimics the accumulation effect in the mathematical model. Mathematically, the time-dependent accumulation variable m(t) in the model is well described and acts like a switch regarding perturbations introduced by brain stimulations. However, m(t) and its relationship with a fast-spiking variable need to be defined better, and the link of m(t) to underlying biophysics should be better described. Additionally, we know that perturbation effects are very specific and depend on various factors, the magnitude of the current pulse, pulse width, electric field distributions, and stimulation frequency tailored to the subject’s response to field oscillations, Excitation-Inhibition balance (Gaba-Glutamate ratio). Those factors have substantially differential effects on the excitability of a network of spiking neurons. Hence, in their phenomenological model, what exactly accumulates as represented by the slow variable here is a bit fuzzy. How these accumulation time scales relate to the dynamics of fast variables could be important for understanding the entry to the seizure state once an appropriate threshold is reached. I find this in the current version of the implementation, and the description is unclear.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "The author mentions local connections are heterogeneous; however, to include that in the virtual brain twin model is nearly impossible at this stage as the pieces of information needed on interneurons and dendritic arborization in clinical measurements have yet to be made available. However, they only consider geometric features of cortical surfaces for the epileptic simulations. It is again unclear what geometric features of cortical surface they are talking about. Do they mean dipole orientation and magnitude scaling as a function of the underlying source location that goes into LED field matrix calculations for SEEG/EEG stimulations? As I understand, they are only using an individual connectome, as shown in the workflow diagram in Figure 1, which incorporates streamlined counts and fibre orientation density measured from DW-MRI.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "The author says we map the stimulus signal onto the parcelated brain areas based on distance. What stimulus they are describing needs to be mentioned. Perhaps that information is important for the readers.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "This is related to the earlier question as well. If I understand their pipeline, the authors have created a virtual brain twin based on the connectivity estimate from patients’ diffusion imaging data. Once they have the virtual brain twin of the individual patient, they will apply a relatively new IACS stimulation technique where vectorial IACS fields are added together, resulting in a T1 field estimate for the brain regions. Subsequently, they used this estimated field as an input to the Isthm parameter and simulated their phenomenological model on one node/vertex on the connectome (from the identified EZ). However, my question is whether the stimulation protocol or, in other words, the T1 field needs to be tailored in an individual/patient-specific manner or whether the individual specificity only lies in the virtual brain twin constructed in the pipeline based on the individual connectome. My conceptual understanding and assumption are that individual connectome requires individual stimulation protocol likely for the most effective clinical outcome of the adjuvant treatment strategy. Please explain what I am missing here.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "For the model inversion using the Hamilton Monte-Carlo method, authors have used a simple normalized prior based on the assumption all the brain regions have the same prior distribution (the prior assumption is that all regions are healthy). Can they use a different prior to estimate posterior probability density and likelihood. All the brain areas/tissues are not healthy. That is the basic presumption and starting point of seizure-like events. Therefore, how a normative prior help in accurately identifying the Posterior distribution of EVs (higher value indicating higher likelihood for seizure) for 8 selected regions obtained from the HMC sampling when analyzing simultaneously SEEG and scalp-EEG above chance level is surprising.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "Even though previous studies reported epileptogenic values, and it is routine in clinics to estimate such numbers, I feel the authors should still mention how these values are calculated. They show multiple plots for the posterior distribution of these values, based on which high chance for seizure locations are identified.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|Human_2|10", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "Is there any clinical ground truth in this approach (ongoing studies mentioned in the discussion section) that at least tells us the predicted location or site of seizure onset matched with what accuracy for the virtual brain simulation-based predictions? Secondly, what is the ground truth or deviation regarding clinically observed brain network Seizure dynamics in those two patients versus those simulated using the Epileptor-Stimulation model through the TI stimulation? This aspect of this study is not very clear. I am wondering whether it is appropriate to calculate a loss function or gradient descent to see whether the stimulation application on the real brain and virtual brain twin is nearly optimized.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|26|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb26", "comment": "The main limitation of the paper is that the simulations of SEEG/TI stimulation were not experimentally validated (i.e., validation was only done by comparing the simulated discovered EZN with the real EZN)).\\n\\nThe paper can be potentially improved by\\n- If SEEG recording under stimulation is available for the patients, compare the simulation to the recording.\\n- Provide insights into the dependency of the seizure activity and/or network span on the stimulation parameters (e.g., frequency and amp).\\n- Compare the amplitude and distribution of the EZN activation under SEEG and Ti stimulations.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|27|Claude|1", "source": "prb", "split": "test", "paper_id": "prb27", "comment": "The paper makes strong mechanistic claims that local wake slow waves (LoWS) \"reduce\" network excitability during interictal epileptiform discharges (IEDs) and serve a \"homeostatic function,\" but the evidence presented is entirely correlational rather than causal.\n\n\"To investigate the negative feed-back of LoWS on IEDs, we used a linear mixed model with delay since the last LoWS and the rate of LoWS in-between two successive IEDs as covariates and HG power during IEDs (from -0.05 to 0.05 s around peak amplitude) as the dependent variable.\"\nThe analysis is purely correlational—it shows associations between variables but cannot establish that LoWS actively reduce excitability. A linear mixed model examining temporal associations does not demonstrate causality. The observed correlation could be explained by multiple alternative hypotheses, including common underlying neural mechanisms that independently influence both LoWS occurrence and IED characteristics.\n\"We found a significant effect of the delay since the last LoWS on HG power during IEDs (β-estimate ± SD: 7.7∙10⁻⁵ ± 1.2∙10⁻⁵ log(µV²/ µV²)/s, p=8∙10⁻¹¹...)\"\nWhile statistically significant, this association cannot distinguish between LoWS causing reduced excitability versus both phenomena being driven by a shared underlying mechanism. The statistical analysis demonstrates co-occurrence patterns but provides no interventional evidence. As established in causal inference literature, correlation does not establish causation, and observational data alone cannot determine causal direction.\n\"This suggests that LoWS also exhibit the second property expected of a homeostatic process: they reduce network excitability, similar to the proposed function of sleep SW.\"\nThe leap from observing a statistical association to claiming that LoWS \"reduce\" excitability represents an overinterpretation of correlational evidence. Proper causal language would acknowledge uncertainty, such as \"LoWS are associated with\" rather than \"reduce.\" This is particularly important because establishing homeostatic function requires demonstrating that perturbations in one direction elicit compensatory responses—evidence the current study design cannot provide.\n\n* Quote from Igelström et al. (2022), J Epidemiol Community Health: \"A current hypothesis states that synaptic homeostasis is underlying sleep homeostasis... Observations of changes in synaptic strength in Drosophila support the hypothesis by providing direct evidence... showing that net synaptic strength increases during extended waking\" [[1]](#ref1)\nIn contrast to the reviewed paper, establishing homeostatic mechanisms typically requires interventional studies or direct measurements of synaptic changes, not merely correlational observations. The foundational work on sleep homeostasis by Tononi and Cirelli [[4]](#ref4) involved experimental manipulations and direct molecular evidence, whereas the current paper relies solely on associational analyses from observational recordings.\n\nReferences:\n[1] [Igelström E, et al. Causal inference and effect estimation using observational data. J Epidemiol Community Health 2022;76:960–966.](https://jech.bmj.com/content/jech/early/2022/09/05/jech-2022-219267.full.pdf)\n[4] [Tononi G, Cirelli C. Sleep and the price of plasticity: from synaptic and cellular homeostasis to memory consolidation and integration. Neuron 2014;81:12–34.](https://www.cell.com/neuron/fulltext/S0896-6273(13)01101-5)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|27|Claude|2", "source": "prb", "split": "test", "paper_id": "prb27", "comment": "The paper uses recordings from patients with Parkinson's disease as a \"control\" group to argue that LoWS are distinct in epilepsy patients, but this comparison is fundamentally flawed because Parkinson's patients have their own neurological pathology and the recordings are from different brain regions (neocortical vs. mesial temporal).\n\n\"Since it was not possible to obtain intracortical, mesial temporal lobe recording in healthy subjects, we examined a dataset of neocortical, electrocorticographic (ECoG) recordings in awake patients with Parkinson's disease using the same detection algorithm.\"\nThe authors acknowledge the fundamental limitation that healthy controls are unavailable, yet proceed to draw strong conclusions about disease-specificity. Using another patient population with a different neurological condition (Parkinson's disease) as a control introduces confounding factors that make interpretation problematic—Parkinson's disease itself affects cortical excitability and oscillatory activity patterns.\n\"We followed the same procedure as the one described for the detection of slow waves in our dataset, except that we did not identify IEDs. None of the 16 patients were suffering from epilepsy (personal communication with Dr. Merk). Data were converted into µV for display. We only used the signal from neocortical contacts.\"\nThe recording sites are fundamentally different: hippocampal/mesial temporal lobe recordings in epilepsy patients versus neocortical ECoG recordings in Parkinson's patients. Regional differences in slow wave characteristics are well-documented in sleep research [[5]](#ref5), making cross-regional comparisons invalid for claims about disease-specificity. This methodological mismatch confounds any conclusions about whether LoWS characteristics differ between epilepsy and non-epilepsy populations.\n\"When plotting all patients in a 2-dimensional space defined by these features, we observed that patients with Parkinson's disease constituted an isolated cluster with low slope and absent down-state.\"\nThe clustering could reflect regional differences (neocortex vs. hippocampus), recording methodology differences (ECoG vs. depth electrodes), or Parkinson's disease pathophysiology itself—not necessarily the absence of epilepsy. The paper does not adequately address these confounds or acknowledge that the observed differences may have nothing to do with epilepsy-specific mechanisms.\n\n* Quote from Sarasso et al. (2020), Brain: \"Local sleep-like cortical reactivity in the awake brain after focal injury\" [[2]](#ref2)\nPrior literature has established that local sleep-like slow waves can emerge during wakefulness after various forms of brain injury, not exclusively in epilepsy. This suggests that LoWS may be a more general phenomenon associated with cortical pathology rather than an epilepsy-specific mechanism, undermining the paper's claim that these waves are uniquely related to epilepsy homeostasis.\n\nReferences:\n[2] [Sarasso S, et al. Local sleep-like cortical reactivity in the awake brain after focal injury. Brain 2020;143:3672–3684.](https://academic.oup.com/brain/article/143/12/3672/5909606)\n[5] [Nir Y, et al. Regional Slow Waves and Spindles in Human Sleep. Neuron 2011;70:153–169.](https://www.cell.com/neuron/fulltext/S0896-6273(11)00149-X)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|27|Claude|3", "source": "prb", "split": "test", "paper_id": "prb27", "comment": "The observed association between higher LoWS rate during retrieval and slower reaction times could be explained by confounding factors such as general arousal state, task difficulty, or time-on-task effects, which were not adequately controlled in the analysis.\n\n\"We found that the rate of LoWS during retrieval was significantly lower during trials with fast versus slow reaction times (RTs; ES, 95% CI: -0.11/s, -0.22 to -0.05, p=0.0114, n=17, Fig. 6a), suggesting that the occurrence of LoWS during retrieval impacts task performance.\"\nThe analysis compares LoWS rates between fast and slow RT trials without controlling for factors known to affect both cognitive performance and neural oscillations. Slow RTs could reflect periods of reduced alertness or lapses in attention, which might independently increase slow wave activity—a confound well-documented in the \"local sleep\" literature that the authors cite. The causal direction cannot be determined from this analysis.\n\"In contrast, the rate of LoWS was similar during good and bad accuracy trials (Fig. 6b).\"\nThe dissociation between RT and accuracy effects is puzzling if LoWS truly cause cognitive impairment through their impact on neuronal activity. If the proposed mechanism were correct, one would expect accuracy to also be affected. The selective effect on RT but not accuracy suggests alternative explanations, such as LoWS reflecting post-response or inter-trial processes rather than causing impaired processing.\n\n* Quote from Vyazovskiy et al. (2011), Nature: \"Local sleep in awake rats... cortical neurons can occasionally show brief periods of silence or Off-periods, just like during sleep, accompanied by slow waves in the local EEG. While some cortical areas may be inactive, other areas remain active, and these periods of 'local sleep' increase with the length of the rats' wakefulness.\" [[3]](#ref3)\nThe foundational \"local sleep\" research demonstrated that periods of local slow wave activity during wakefulness increase with time awake and are associated with performance errors. However, this relationship reflects fatigue and sleep pressure, not necessarily a distinct epilepsy-related homeostatic mechanism. The current paper does not adequately distinguish whether LoWS-associated cognitive effects reflect epilepsy-specific processes versus general vigilance fluctuations.\n\nReferences:\n[3] [Vyazovskiy VV, et al. Local sleep in awake rats. Nature 2011;472:443–447.](https://www.nature.com/articles/nature09567)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|27|Claude|4", "source": "prb", "split": "test", "paper_id": "prb27", "comment": "The observed negative correlation between LoWS rate and IED rate (r²=0.51, p=0.002) could reflect mutual inhibition, a common underlying mechanism, or detection artifacts, yet the paper interprets this finding as supporting the homeostasis hypothesis without adequately considering alternative explanations.\n\n\"We next determined the rate of LoWS against that of IEDs. We observed a significant negative correlation across patients (Pearson correlation, r²=0.51, p=0.002, n=16, Fig. 3d, see Supplementary Information for further discussion).\"\nA negative correlation between LoWS and IED rates is equally consistent with multiple mechanistic models: (1) LoWS suppress IEDs (the authors' interpretation); (2) IEDs suppress LoWS generation; (3) both phenomena compete for the same underlying neural substrate; or (4) methodological overlap in detection (periods of high slow wave activity might reduce IED detection sensitivity and vice versa). The correlation alone cannot distinguish between these alternatives.\n\"If LoWS were mislabeled IEDs, and since LoWS detection is semi-automatic (except for the visual removal of artefacts and post-IED waves), then the proportion of mislabeled IEDs as LoWS should be constant across participants, resulting in a positive correlation (we provide further discussion of this point, as well as statistical confirmation, in the Supplementary Information).\"\nWhile the authors address the mislabeling concern, the negative correlation itself has an alternative interpretation: patients with more severe epilepsy (higher IED rates) may have less opportunity for LoWS to occur due to near-continuous pathological activity. This would produce a negative correlation without implying any homeostatic function, instead reflecting a ceiling effect on neural activity patterns.\n\"Besides LoWS rate, neither the slope (Pearson correlation, r²<0.001, p>0.99, n=16, Extended Data Fig. 5a), nor the amplitude (Pearson correlation, r²<0.001, p=0.96, n=16, Extended Data Fig. 5b) of LoWS correlated with the IED rate.\"\nThe lack of correlation between LoWS characteristics (slope, amplitude) and IED rate is inconsistent with a simple homeostatic model, where one might expect patients with higher IED rates to show adapted LoWS features (steeper slopes, larger amplitudes) as a compensatory response. This null finding is difficult to reconcile with the proposed homeostasis hypothesis and suggests the relationship between LoWS and IEDs may be more complex than the straightforward mechanistic model proposed.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|27|GPT|1", "source": "prb", "split": "test", "paper_id": "prb27", "comment": "The paper’s inference that LoWS are “protective” because LoWS rate is negatively correlated with IED rate is not valid, because the LoWS detection pipeline systematically removes slow waves near IEDs and the proposed “corrected rate” (used to compare cohorts) is mathematically unjustified; this compromises the LoWS–IED association component of the Results and downstream interpretation.\n\n“Next, any candidate slow waves that occurred ≤1 s after a detected IED on any of the recording contacts in the same brain region were discarded.”\nThis exclusion rule mechanically reduces the counted LoWS whenever a subject has more IEDs, because more IEDs create more excluded time around discharges and more opportunities for candidate slow waves to be discarded. Even if LoWS and IEDs were truly independent physiological processes, conditioning LoWS detection on proximity to IEDs can induce an artificial anticorrelation in observed rates across patients. The paper later interprets the observed negative correlation as evidence of a protective mechanism, but this rule makes that interpretation unsafe without an explicit correction that accounts for removed observation time and detection censoring. The issue is not minor: the exclusion window is applied “on any of the recording contacts in the same brain region,” which can remove substantial data in high-IED recordings. A rigorous approach would report effective analyzed time, adjust rates for censored intervals, and demonstrate that the LoWS–IED rate relationship persists when accounting for this deterministic removal.\n“We observed a significant negative correlation across patients (Pearson correlation, r2=0.51, p=0.002, n=16, Fig. 3d…”\nThis sentence describes the key empirical pattern that the paper later uses to support a “protective” LoWS interpretation, so any bias in how LoWS rates are constructed directly threatens the conclusion. Because the paper’s LoWS counts are partly defined by excluding events near IEDs, the correlation is not a clean observation about two independently measured rates. The paper does not quantify how much data are removed per patient by the IED-linked exclusion, which is essential to judge whether the anticorrelation could be a measurement artifact. Moreover, correlating per-patient rates ignores within-patient temporal dependencies and state changes (task phase, vigilance, medication timing) that could jointly modulate both event rates. Without showing robustness to censoring-aware rate estimation, the observed anticorrelation cannot be treated as evidence that “patients with fewer protective LoWS” have more IEDs.\n“The corrected rate was calculated by multiplying the LoWS rate by the IED rate (Extended Data Fig. 4c, 2 last columns), to account for the negative correlation between these variables.”\nMultiplying two negatively correlated rates does not “correct” one for the other in any standard statistical sense; instead it creates a new composite quantity with unclear interpretation and units (rate²). If the goal is to compare LoWS burden across cohorts while controlling for IED-related censoring or confounding, the correction should be based on modeled censoring (e.g., subtracting excluded time) or regression adjustment, not an ad hoc product. This matters because the paper uses this “corrected rate” to argue that cohort differences in LoWS frequency disappear after accounting for IED rate, which is a substantive conclusion about reproducibility across datasets. Because the correction is not tied to an identifiable estimand (e.g., LoWS rate per effective clean time), the comparison can be misleading even if numerically “similar.” A reader cannot reconstruct or validate the intended adjustment logic, which undermines confidence in the claimed cross-cohort normalization.\n“While filtering has the potential to substantially increase the number of discoveries, its validity has been debated. One criticism is that data-based filtering constitutes a statistical test. Ignoring this fact, and computing and adjusting the remaining p-values as if filtering had not taken place, may result in overly optimistic adjusted p-values and a true false positive rate which is larger than reported.” [[2]](#ref2)\nAlthough this quote arises in the context of high-throughput hypothesis testing, it articulates a general principle: selection or filtering based on the data-generating process can invalidate downstream inference if not explicitly incorporated into the analysis. In the reviewed paper, LoWS are “filtered” by proximity to IEDs, which is a data-driven rule tied to the very outcome (IEDs) that the paper then relates to LoWS rate. The paper’s approach similarly risks producing an “optimistic” association between LoWS and IEDs (here, an anticorrelation interpreted as protection) because the selection mechanism is not modeled. The key parallel is that conditioning changes what the remaining events represent, so naive summaries (like raw rates and correlations) can be biased. This literature therefore supports the critique that the paper should either avoid such conditioning for the specific analysis or use methods that explicitly account for the selection/censoring mechanism. Without that, the strength and even direction of the reported LoWS–IED relationship are not reliably interpretable.\n\nReferences:\n[2] [Bourgon R, Gentleman R, Huber W. Independent filtering increases detection power for high-throughput experiments. *PNAS* (2010).](https://www.pnas.org/doi/10.1073/pnas.0914005107)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|27|GPT|2", "source": "prb", "split": "test", "paper_id": "prb27", "comment": "The paper’s conclusion that LoWS reduce increases in network excitability during IEDs (and the broader “epilepsy homeostasis hypothesis”) is not robustly supported because it is inferred from correlational mixed-model associations and modeling choices that do not establish directionality or rule out plausible confounding in the LoWS–IED interaction analyses.\n\n“Importantly, we also provide evidence that LoWS reduce increases in network excitability during IEDs…”\nThis statement asserts a directional, protective effect (“reduce”) that implies a causal mechanism rather than a mere association. However, the paper’s described analyses are observational and do not include any experimental manipulation or quasi-experimental identification strategy that would justify causal language. Because patients are undergoing clinical monitoring with variable brain states, medication regimens, and pathology, both LoWS occurrence and IED expression could be driven by unmeasured state variables. The paper does not present design elements commonly used to strengthen causal interpretations from observational electrophysiology, such as within-subject causal estimands with strong time-series controls, instrumental variables, or intervention-like perturbations. As a result, the phrasing in the abstract overstates what the study design can support. A more defensible conclusion would describe conditional associations (e.g., LoWS timing correlates with HG during IEDs) while explicitly acknowledging alternative explanations.\n“Thus, a longer delay since the last LoWS is associated with high network excitability during IEDs (and vice versa)… This suggests that LoWS also exhibit the second property expected of a homeostatic process: they reduce network excitability…”\nThe quoted passage explicitly moves from an association (“is associated”) to a mechanistic inference (“reduce network excitability”), which is a logical leap without stronger identification. Temporal ordering alone (LoWS occurring before an IED) does not guarantee that LoWS causally attenuate the subsequent HG burst, because both can be downstream of a latent excitability trajectory or vigilance fluctuations. Additionally, “delay since last LoWS” is itself an endogenous variable shaped by the rate of LoWS and by any censoring rules tied to IEDs, so it is not a clean exposure. The analysis could also reflect reverse causality in the sense that impending large IEDs occur during periods when LoWS are less likely to appear, rather than LoWS actively suppressing IED-related excitability. The paper does not provide falsification tests (e.g., negative controls) that would help discriminate these interpretations. Therefore, the evidence supports at most a predictive relationship, not a demonstrated negative feedback mechanism.\n“Then, we used a linear mixed model with HG power during the IED as the dependent variable and delay since the last LoWS, rate of LoWS, interaction [baseline increases in HG*delay] and [baseline increases HG*rate] as covariates. We did not include “baseline increases in HG” as an independent covariate…”\nThis modeling decision is consequential because baseline HG changes are plausibly a direct driver of both IED generation and IED-associated HG magnitude, and omitting a main effect while including interactions can yield coefficients that are difficult to interpret causally. The justification given (“it can be expected that an increase in HG power will be followed by high values of HG”) is an argument for including baseline HG as a confounder rather than excluding it, especially when the goal is to isolate any LoWS-specific association. Moreover, the model uses a fixed far-baseline window (“-250 to -245 s”) that may not exist uniformly across IEDs or may select specific subsets of events, which can introduce additional selection effects in time-series data. The paper does not report sensitivity analyses showing that conclusions remain stable under alternative baseline definitions or with baseline HG included as a covariate. Because the central “negative feedback” claim depends on this model, these choices undermine the robustness of the conclusion. At minimum, the paper should show that the key coefficients are not artifacts of model specification.\n“In an ideal world, all policy and clinical decisions would be based on the findings of randomized experiments.” and “While causal inferences from observational data are always risky, an appropriate analysis of observational studies often results in the best available evidence…” [[3]](#ref3)\nThis quote articulates a standard methodological caution: observational evidence can be informative but does not automatically justify causal conclusions without strong assumptions. The reviewed paper’s strongest claims about “reducing” excitability and “negative feed-back” are precisely causal claims made from observational recordings in clinical patients. The authors do not articulate the causal assumptions required for their inference (e.g., no unmeasured confounding of LoWS timing and IED HG magnitude), nor do they provide analyses that would make those assumptions more plausible. The quote therefore supports the criticism that the paper should either downgrade its causal language or substantially strengthen its identification strategy. Importantly, this is not a stylistic point: causal overreach can mislead readers about what kinds of interventions (e.g., promoting LoWS) the data actually justify. The paper itself notes a need for future interventional testing, which further underscores that the current evidence is not yet causal.\n\nReferences:\n[3] [Hernán MA. Miguel Hernan (Harvard T.H. Chan School of Public Health) biography page (accessed 2026-01-07).](https://www.hsph.harvard.edu/miguel-hernan/causal-inference-book/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|27|GPT|3", "source": "prb", "split": "test", "paper_id": "prb27", "comment": "The paper’s claim that LoWS are distinct from slow waves in “people without epilepsy” is not well supported because the comparator cohort is Parkinson’s disease patients recorded with neocortical ECoG (different pathology, brain region, and recording modality), and the analysis omits key steps (e.g., IED detection) that affect comparability.\n\n“LoWS were distinct from slow waves recorded in people without epilepsy…”\nThis sentence makes a strong cross-population claim that implies differences are attributable to epilepsy rather than to other factors. However, “people without epilepsy” in this manuscript are not healthy controls; they are patients with Parkinson’s disease undergoing neurosurgical ECoG recordings. Parkinson’s disease is itself a neurological disorder associated with altered cortical-subcortical dynamics, so it is not a neutral baseline for claims of epilepsy specificity. Additionally, the recording site differs (neocortex vs mesial temporal lobe/hippocampus), and slow-wave characteristics are known to vary across brain regions, which can easily create apparent clustering differences. Without a matched control recorded in comparable regions and with similar acquisition conditions, the observed differences cannot be confidently attributed to epilepsy. Therefore, the paper overgeneralizes from an unmatched comparator.\n“Since it was not possible to obtain intracortical, mesial temporal lobe recording in healthy subjects, we examined a dataset of neocortical, electrocorticographic (ECoG) recordings in awake patients with Parkinson’s disease… using the same detection algorithm.”\nThis quote confirms that the comparator differs simultaneously in recording location (neocortex vs hippocampus) and modality (ECoG vs depth electrodes), both of which affect measured waveforms, signal-to-noise, and spatial sampling. Using the “same detection algorithm” does not ensure that detected events are physiologically comparable when the underlying signals and electrode geometries differ. The paper’s own discussion concedes that the Parkinson’s data were obtained from neocortical surface recordings, but it still uses this dataset to argue that Parkinson’s slow waves form an “isolated cluster” with “absent down-state,” implying a meaningful biological difference. Because electrode type and referencing can strongly affect measured slope and apparent HG “down-state,” modality confounding is a serious threat. The paper does not present harmonization analyses (e.g., region-matched epilepsy neocortex vs Parkinson neocortex, or simulations of electrode sensitivity) that would mitigate this concern. Thus, the conclusion that epilepsy LoWS are “distinct” from non-epileptic waves is not securely supported.\n“We followed the same procedure as the one described for the detection of slow waves in our dataset, except that we did not identify IEDs… We only used the signal from neocortical contacts.”\nThe omission of IED identification in the Parkinson cohort undermines comparability because the epilepsy cohort’s LoWS pipeline explicitly discards candidate slow waves near IEDs, whereas the Parkinson cohort cannot apply that exclusion. This means the retained event sets may reflect different mixtures of physiological and pathological waveforms, even if Parkinson patients have no epilepsy. The paper also restricts Parkinson data to neocortical contacts, while key epilepsy analyses focus on hippocampal contacts, making “cluster” separation potentially a trivial result of anatomical differences. Furthermore, if the goal is to show that LoWS are an epilepsy-specific adaptation, using a comparator with different task context, different hardware, and a different disease state creates multiple uncontrolled degrees of freedom. At minimum, the paper should frame this comparison as suggestive rather than definitive. As written, it is insufficient to justify the abstract-level claim about distinction from “people without epilepsy.”\n“Electrocorticography (ECoG) offers a powerful approach by capturing neural activity directly from the cortical surface via electrodes placed beneath the skull…” [[5]](#ref5)\nThis quote establishes that ECoG is fundamentally a surface recording technique with specific spatial sensitivity and signal properties. In the reviewed paper, the “non-epileptic” comparator uses neocortical ECoG, whereas the epilepsy cohorts emphasize mesial temporal depth recordings, so the measured waveforms and derived features (slope, HG changes) are not directly comparable. Even if the same detection parameters are applied, the effective filtering and spatial averaging differ across modalities, affecting amplitude distributions and therefore percentile-based thresholds. This provides a concrete methodological basis for why observed differences in “detectability,” slope, and “down-state” could arise from instrumentation and geometry rather than from epilepsy-specific physiology. The paper does not quantify or control for these modality effects, so the comparison is confounded. Consequently, the evidence supports the criticism that the claimed epilepsy-specific distinction is overstated.\n“Unlike ECoG, sEEG is not limited to the surface of the cortex, and allows for sampling from distant cortical and subcortical regions…” [[4]](#ref4)\nThis quote highlights that sEEG and ECoG have different anatomical access and sampling characteristics, which implies that waveform features cannot be compared as if they came from the same measurement system. The reviewed paper’s epilepsy LoWS are detected largely in hippocampal depth recordings, where local generators and volume conduction differ markedly from surface ECoG signals in Parkinson’s disease patients. Because the paper’s “distinctness” analysis uses slope and HG-defined “down-state” as axes, any systematic modality- and region-dependent scaling will affect clustering in that feature space. The quote therefore supports the methodological concern that the Parkinson-vs-epilepsy separation may reflect recording constraints rather than true population differences in slow-wave physiology. Without a region- and modality-matched control, the conclusion about uniqueness to epilepsy is not well grounded. This is a substantive limitation because the claim appears in the abstract and motivates the paper’s novelty.\n\nReferences:\n[4] [Jensen MA, Schalk G, Ince N, Hermes D, Worrell GA, Brunner P, Staff NP, Miller KJ. sEEG-based brain-computer interfacing in a large adult and pediatric cohort. *Journal of Neural Engineering* (2025).](https://iopscience.iop.org/article/10.1088/1741-2552/ae2955)\n[5] [Hu Y, Zhang B, Hu Z, Liu X, Li X, Dai J. The Application of an Ultra-Thin, High-Density μECoG Array in Dissecting Caffeine-Induced Cortical Dynamics in Mice. *Sensors* (2025) (PMC full text).](https://pmc.ncbi.nlm.nih.gov/articles/PMC12737276/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|27|GPT|4", "source": "prb", "split": "test", "paper_id": "prb27", "comment": "The paper’s statistical reporting is not sufficiently reliable because it asserts that multiple-comparisons correction is unnecessary under “estimation statistics,” yet it repeatedly uses p-values (including many across figures and analyses) as confirmatory evidence; this undermines confidence in claimed effects across the Results and Online Methods.\n\n“Since estimation statistics are not null-hypothesis testing, they do not require correction for multiple comparisons.”\nThis statement is problematic because the paper still computes and interprets p-values throughout the manuscript, including for many distinct outcomes (rates, slopes, amplitudes, HG measures, behavioral associations). Regardless of philosophical framing, when p-values are used to decide whether an effect is “significant” or to support claims of effects existing, multiplicity remains a concern because repeated testing increases the chance of observing small p-values under noise. The paper mixes estimation language (“effect size”) with repeated confirmatory inference (“p=…”, “significant”), which can mislead readers about the evidential strength of findings. The authors do mention a post hoc check that some p-values “resisted” Bonferroni-Holm correction, but they do not provide a complete accounting of the full family of tests that would be needed for rigorous control. Moreover, several analyses use different statistical paradigms (permutation t-tests, Wilcoxon tests, mixed models) without a unified multiplicity plan, which makes overall error control opaque. This undermines the reliability of conclusions drawn from a collection of p-values.\n“We found that all p-values remained significant.”\nThis sentence suggests confirmatory robustness, but it does not specify which p-values were included, how families of comparisons were defined, or whether the reported list covers all inferential claims in the Results. Because the paper spans multiple datasets (UCL epilepsy, Boran epilepsy, Parkinson’s ECoG), multiple dependent measures (rate, slope, amplitude, HG), and multiple behavioral outcomes (RT, accuracy), the number of potential comparisons is large. A statement of universal robustness without transparent enumeration can give a false sense of certainty, especially when some analyses (e.g., clustering distances, mixed models) are not naturally covered by the same correction logic. Additionally, the paper’s own methods include choices that can increase researcher degrees of freedom (time windows, normalization choices, event selection), which further increase the risk of selective reporting if not pre-registered. Without full disclosure of all tested hypotheses and their correction, readers cannot evaluate the true false positive risk. Therefore, this claim does not adequately establish statistical reliability.\n“Because a large number of hypothesis tests are performed in such variable-by-variable analyses, many true-null hypotheses will produce small p-values by chance. As a consequence, numerous false positives, or type I errors, will result if p-values are compared to standard single-test thresholds.” [[2]](#ref2)\nThis quote states the core multiplicity problem: repeated testing can generate apparently “significant” findings even when null effects are true. The reviewed paper’s Results and Online Methods report many p-values across multiple measures and datasets, yet it asserts that correction is not required under its chosen framework. Even if the authors emphasize effect sizes, they still use p-values as evidence that effects exist and survived “stringent criteria,” which is exactly the context where multiplicity matters. The quote therefore directly contradicts the implication that one can safely interpret many p-values without a clear multiplicity strategy. Importantly, this concern affects interpretability of borderline effects (e.g., p≈0.01–0.03) and complex models with multiple covariates and interactions, which are prominent in the LoWS–IED analyses. A more standard practice would predefine primary endpoints and apply appropriate control across secondary/exploratory tests. Because the manuscript does not do this transparently, the reliability of several statistical claims is weakened.\n\nReferences:\n[2] [Bourgon R, Gentleman R, Huber W. Independent filtering increases detection power for high-throughput experiments. *PNAS* (2010).](https://www.pnas.org/doi/10.1073/pnas.0914005107)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|27|GPT|5", "source": "prb", "split": "test", "paper_id": "prb27", "comment": "The paper’s computational reproducibility is substantially limited because it claims analyses rely on custom MATLAB code but provides only incomplete, non-runnable scripts with undefined inputs and variables, preventing independent reproduction of the core detection pipeline and downstream analyses.\n\n“Analyses were performed using custom Matlab (The MathWorks, v. 2022a) code and the Fieldtrip toolbox.”\nThis statement implies that the central results depend on a computational pipeline, so reproducibility requires access to runnable code (or at least complete pseudocode) that implements the described analyses. However, the repository provided alongside the preprint contains only a small set of MATLAB scripts and does not include the end-to-end pipeline for figures, statistics, or dataset processing. The paper also relies on multiple external tools (FieldTrip, estimationstats.com, Prism, SPSS), making it especially important to provide executable scripts that record parameter choices and exact preprocessing steps. Without a complete pipeline, key analytic degrees of freedom (filter design, thresholds, artifact rejection, referencing) cannot be audited or replicated. This is a major issue because the main claims rest on event detection and time-locked HG/spiking analyses that are sensitive to preprocessing. In practice, the described “custom Matlab” approach cannot be independently verified from the materials provided here.\n```matlab\nrawdata                             = ;          % lines are electrodes, columns are timeframes\nn                                   = ;          % filter order\nsf                                  = ;          % sampling frequency\nfc_low                              = 0.5;       % high-pass for SW detection\nfc_high                             = 4;         % low-pass for SW detection\nmin_duration_ZeroCrossing_sec       = 0.25;      % minimal duration of a half-wave, in s\nmax_duration_ZeroCrossing_sec       = 1;         % maximal duration of a half-wave, in s\nkeep_above_prctle                   = [];        % threshold above which candidate waves are saved\n```\nThis code block (from the slow-wave detector) contains placeholders for essential inputs (raw data, filter order, sampling frequency) rather than a function signature or runnable script that accepts parameters. As written, it cannot be executed, which prevents reviewers from validating the exact detection logic described in the paper (e.g., the 0.5–4 Hz band, 0.25–1 s duration, amplitude thresholding). Additionally, setting `keep_above_prctle = [];` is not a meaningful operational threshold in MATLAB for percentile selection, and the script does not define how this value should be set to the “90th percentile” described in the manuscript. Because the paper’s claims about LoWS depend critically on detection fidelity (distinguishing LoWS from IED-related waveforms), incomplete detection code is a major reproducibility gap. This is not a minor documentation issue; it prevents independent confirmation of the event extraction underpinning all subsequent analyses. A reproducible release would provide callable functions with defined inputs, example usage, and parameter files corresponding to the reported analyses.\n```matlab\nsf                              = ;      % sampling frequency of the file\nfilter_order                    = ;      % order of the filter\n...\ncd('Your directory for supplementary scripts\\');\n```\nThis code block (from the IED detector) again includes undefined required parameters (`sf`, `filter_order`) and hard-coded, non-portable assumptions about the execution environment. The script also references variables such as `eegData` later in the file without defining or loading them, indicating that substantial missing context is required to run the detector. Since the paper uses IED detection both to exclude nearby slow waves and to analyze LoWS–IED interactions, inability to reproduce IED detection undermines reproducibility of core results. The paper describes semi-automated detection with visual curation, but it does not provide the tooling or interfaces needed to replicate that curation process and its outputs. Without runnable code and example data, independent researchers cannot assess sensitivity to threshold choices (e.g., 3.5× and 4× envelopes) or validate the reported IED rates. This constitutes a substantive reproducibility limitation.\n“Last, but not least, all input data, scripts, versions, parameters, and intermediate results should be made publicly and easily accessible.” [[1]](#ref1)\nThis widely cited reproducibility guidance directly conflicts with the state of the provided code materials, which lack runnable scripts, defined parameters, and documented intermediate outputs. The reviewed paper’s main conclusions depend on many analytical steps (event detection, exclusion criteria, HG estimation windows, mixed models) where small implementation differences can materially change outcomes. Making “scripts, versions, parameters, and intermediate results” available is especially critical for intracranial electrophysiology studies, where preprocessing and artifact handling are complex and underdetermined. The quote supports the critique that, without complete code and parameterization, peers cannot realistically reproduce the analyses even if they had access to similar data. While clinical data sharing can be constrained, code and synthetic or minimally sufficient example data could still be shared to validate the pipeline. The current materials fall well short of this standard, which undermines transparency and reproducibility.\n\nReferences:\n[1] [Sandve GK, Nekrutenko A, Taylor J, Hovig E. Ten Simple Rules for Reproducible Computational Research. *PLOS Computational Biology* (2013).](https://journals.plos.org/ploscompbiol/article?id=10.1371/journal.pcbi.1003285)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|27|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb27", "comment": "The manuscript fails to convincingly demonstrate that \"Local Wake Slow Waves\" (LoWS) are a distinct physiological phenomenon rather than the slow-wave component of interictal epileptiform discharges (IEDs) or other pathological epileptic transients.\n\n\"We excluded any slow waves associated with (i.e., within 1 s of) an IED and took several confirmatory steps to ensure that the identified slow waves were not mislabeled IEDs\"\nThe exclusion of IEDs relies on imperfect automated detection and subjective visual inspection. Since IEDs (spike-and-wave complexes) are characterized by a spike followed by a slow wave with a down-state (neuronal silence), any IED where the spike is missed by the detector (e.g., due to low amplitude or electrode placement) will be classified as a \"LoWS\". The fact that LoWS share the key feature of IED waves (the down-state) strongly suggests they may simply be \"spike-less\" IEDs or IEDs with undetected spikes.\n\"patients with Parkinson’s disease constituted an isolated cluster with low slope and absent down-state.\"\nThe authors admit that LoWS (defined by high slope and down-state) are essentially absent in non-epileptic controls (Parkinson's patients). This absence in controls strongly supports the interpretation that LoWS are an epilepsy-specific pathological phenomenon (e.g., interictal slow activity) rather than a physiological \"wake slow wave\" mechanism that is merely \"recruited\" in epilepsy.\n\"Importantly, the peak of HG associated with IEDs was significantly higher than that during pSW\"\nThe authors attempt to distinguish LoWS from IEDs by comparing the high-gamma (HG) power of the IED spike to the LoWS positive wave (pSW). This is a flawed comparison because IEDs are defined by high-frequency spiking activity. A valid comparison would be between the HG power during the *slow wave component* of a confirmed IED and the LoWS. The lack of this comparison undermines the claim that LoWS are mechanistically distinct from the wave component of IEDs.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|27|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb27", "comment": "The provided code and methodology are insufficient to reproduce the detection of LoWS and their separation from IEDs, which is the central methodological challenge of the paper.\n\n```matlab\n% For simplicity, we remove the condition \"no_IED_before\", and assume that\n% the post-processing pruning controls for that\n```\nThe provided code `iDetectSlowWave.m` explicitly removes the step that excludes slow waves preceded by IEDs. Since the distinction between LoWS and IEDs is the most critical aspect of the study, the omission of this step in the provided code renders the results non-reproducible. The \"post-processing pruning\" script is not provided.\n\"The second step asks the reviewer to refine the detection. ... From here on, use data.POS_IED and data.NEG_IED for the visual confirmation.\"\nThe IED detection script `iFindIED_semiautomatic.m` relies on a manual \"visual confirmation\" step that is not scripted or standardized. This subjective element makes it impossible for independent researchers to replicate the exact set of excluded IEDs and, consequently, the set of identified LoWS.\n\"We were concerned by the fact that IEDs are typically followed by a slow wave, but it was not possible to visually inspect all slow waves, due to the large number detected.\"\nThe authors admit they could not visually inspect all slow waves, yet they rely on visual inspection to confirm LoWS are not mislabeled IEDs. This inconsistency, combined with the lack of automated exclusion code, raises significant concerns about the purity of the LoWS dataset.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|27|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb27", "comment": "The abstract states the hypothesis that “slow waves are activated in epilepsy to reduce aberrant activity”. On one hand the authors claim that the local wake slow waves (LoWS) are a normal phenomenon, but here that say that they are “activated in epilepsy”. I do not think they have demonstrated that LoSW are more frequent in epilepsy than in healthy brain or are in any way “activated”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|27|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb27", "comment": "The issue remains that the rarity of wake slow wave is not a result but is a necessary consequence of the definition (top 10%). If the denominator is the number of slow waves detected during the wake period analyzed, they will necessarily find that LoSW are rare. They could not find, for instance, a frequency of 0.4/s/channel. They find this type of rate in N3 of the MNI dataset because I assume they took the top 10% of all slow waves recorded during the different stages of sleep. If they normalized separately for each state, they would find that slow waves are rare in all sleep stages, including N3. It must be clear that rarity of wake slow waves is not a finding of this study, which studies the properties of a small selection of slow waves, the largest ones. The first section of the results should be modified and the influence of the definition of slow waves must be discussed.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|27|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb27", "comment": "Then the conclusions should clearly be limited to the temporal lobe. In the MNI dataset, as in this dataset, the LoSW are rare by construction. The authors can conclude that they are less frequent in wake than in N3 from the MNI data, but in fact they are not also not frequent in N2.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|27|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb27", "comment": "I was asking for the high pass filter, not the low pass, which is much less important in the context of this study. If the high-pass is too high, it could interfere with the detection of slow waves and this should be discussed.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|27|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb27", "comment": "The authors did not explain how they assessed that the patients were awake. If there was a direct assessment, it should be explained. If there was no direct assessment, then they should say that the assessment was done by comparing parts of the spectrum between the task period and the presumably awake period. The absence of a statistically significant difference (particularly with a p=0.07) is of course not a proof of similarity. This an important issue because the authors describe an unusual phenomenon which, they claim, occurs during wakefulness. One must know how this was assessed and the possible uncertainties in this process.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|27|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb27", "comment": "Information about the reference is still not given, even in the section called “choice of the reference”. Where is the reference?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|27|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb27", "comment": "The manuscript was not modified to reflect the authors’ answer. If the visual override included spikes within 1 s of an automatic detection, what is the purpose of this 1s refractory period? Is it meaningless?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|27|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb27", "comment": "the authors can keep these sections but should make it clear that the absence of correlation only indicates that the majority of LoSW are not IEDs, not excluding the possibility that some LoSW are mislabeled IEDs.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|27|Human_1|9", "source": "prb", "split": "test", "paper_id": "prb27", "comment": "The increase of slope and amplitude of the LoSW are so small that it is important to make sure they are not just correlated to passing fime (since last sleep, unfil next sleep). It would be easy and useful to place randomly fake LoSW at the same average rate as LoSW and verify that the changes are then absent.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|27|Human_1|10", "source": "prb", "split": "test", "paper_id": "prb27", "comment": "The authors argue that they occur at a rate similar to changes occurring during a night. This is indeed a very small change if considered over 1 to 3 min. Does it have a pracfical effect?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|27|Human_1|11", "source": "prb", "split": "test", "paper_id": "prb27", "comment": "With respect to the change in gamma power as a funcfion of durafion since the last LoSW, it is difficult to appreciate its magnitude. Could it be given, like the slope, in %/min? Could the authors comment on the funcfional significance of this magnitude, i.e. does this change have a chance to visibly alter the number or “size” of IEDs?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|27|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb27", "comment": "The additional analyses presented to clarify the difference between LoWS and lesional focal slowing are appreciated. The interpretation of these findings would benefit from further measured discussion. It is still unclear to me whether the authors posit that LoWS are induced by the abnormal network dynamics that are a consequence of epilepsy, or if they are a physiologic phenomenon that also occurs in epilepsy. The wording “healthy brain regions” and “not restricted to epileptic brain regions” (pg. 5, line 128-130) seems to argue for the latter. Do LoWS still play a homeostatic role in this case? The assignment of LoWS as key components of epilepsy homeostasis (pg 10, line 321) is more in keeping with the former. I understand it is a complex issue, but this is a central point of the manuscript.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|27|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb27", "comment": "Although mechanistic experimentation is beyond the scope of the manuscript, some discussion of how the authors hypothesize that LoWS induce relatively long-lasting changes in network excitability should be included. For instance, it is conceivable that the occurrence of a LoWS could actually be hypersynchronizing by causing a strong reduction in firing rate across the population simultaneously. How would this decrease the likelihood of subsequent hypersynchronous phenomena (IEDs)? Such a discussion would be helpful to frame future mechanistic studies to understand the authors’ observed correlations.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|27|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb27", "comment": "The ‘n’ used for each analysis should be presented somewhere (either in the Results text or figure legends, but in a consistent manner). Can the authors confirm in the manuscript that the linear mixed models used incorporate patients as a grouping variable to ensure that datapoints from a restricted subset of patients are not driving the overall calculated effect size.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Claude|3", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "While the gLV model is used to provide theoretical support for experimental findings, the model uses randomly sampled interaction matrices rather than parameters fitted to or constrained by the actual experimental data, limiting the ability to claim that the model mechanistically explains the observed phenomena.\n\n\"We sampled the interaction strength from a uniform distribution U [0, 2<α_{ij}>], where <α_{ij}> is the mean interaction strength between species (predictions of this model are insensitive to the particular distribution chosen)\"\nThe model employs randomly drawn interaction coefficients from a specified distribution, with no attempt to fit these parameters to actual experimental data or constrain them using measured species abundances. While this approach is common in theoretical ecology for exploring general patterns [[5]](#citation-list), it limits the model's predictive power for specific experimental systems. The claim that the model \"predicts\" experimental observations is weakened when the model parameters are not derived from or validated against the data being explained.\n\"Modeling species interactions as a random interaction network captures species heterogeneity without assuming any particular community structure\"\nModern approaches to microbial community modeling often involve inferring gLV parameters from time-series abundance data to enable quantitative predictions [[6]](#citation-list). The paper's approach of using random matrices provides qualitative agreement but cannot distinguish whether the specific dynamical regimes observed in experiments arise from the same mechanisms operating in the model. The experimental communities may have structured interactions (e.g., based on phylogenetic relatedness, metabolic complementarity, or pH modification abilities) that differ systematically from random networks.\n\"Consistent with experiments (Fig. 1c), the invasion probability of simulated resident communities positively correlates with their richness, which arises because fluctuating communities are more diverse and more invasible.\"\nThe agreement between model and experiment is characterized as \"consistent\" in a qualitative sense—both show positive diversity-invasibility correlations under certain conditions. However, quantitative comparisons of effect sizes, invasion probabilities, or the distribution of dynamical states are not presented. Without such quantitative validation, the model serves more as a conceptual illustration than as a validated mechanistic explanation of the specific experimental results.\n\nReferences:\n[5] Bunin G (2017). Ecological communities with Lotka-Volterra dynamics. *Physical Review E* 95: 042414. https://journals.aps.org/pre/abstract/10.1103/PhysRevE.95.042414\n[6] Remien CH, Eckwright MJ, Ridenhour BJ (2021). Structural identifiability of the generalized Lotka-Volterra model for microbiome studies. *Royal Society Open Science* 8: 201378. https://royalsocietypublishing.org/doi/10.1098/rsos.201378", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Claude|4", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "The paper emphasizes resident community properties as the primary determinants of invasion success while downplaying invader identity, yet the data reveal that 2 of 9 invader species (Pseudomonas and Enterobacterales) account for the majority of successful invasions, suggesting invader traits may be more important than acknowledged.\n\n\"we did not observe a significant correlation between a species' ability to invade and that species growth in monoculture... Pseudomonas (invader 4) and Enterobacterales (invader 7) were the two most successful invader species (16/35 and 6/11 invasions, respectively)\"\nThe two species mentioned account for 22 out of approximately 62 successful invasions reported across all conditions, representing a highly uneven distribution of invasion success among invaders. If resident community properties were the sole drivers, invasion success would be more evenly distributed across invader species. The fact that Pseudomonas succeeded in 45.7% (16/35) of its invasion attempts while some other species had near-zero success rates indicates substantial invader-specific effects that the analysis does not fully address.\n\"The phylogeny of invader 1 to invader 9 are: Flectobacillus, Pseudomonas, Pedobacter, Pseudomonas, Pantoea, Bacillus, Enterobacterales, Pantoea, Chryseobacterium.\"\nOnly 9 invader species were tested, with two Pseudomonas strains and two Pantoea strains included. This limited invader diversity, combined with the dominance of particular taxa among successful invasions, raises questions about the generalizability of the conclusions. Invasion ecology literature emphasizes that invader traits such as ecological versatility, competitive ability, and growth strategies are important determinants of invasion success [[7]](#citation-list), and testing only 9 species limits the ability to control for these factors.\n\"we therefore found that monoculture growth properties were surprisingly ineffective at predicting the success of a species as an invader, while resident community properties are the primary factors determining the invasion outcome.\"\nWhile monoculture growth rate may not predict invasion success, this does not exclude other invader traits (such as interaction profiles, toxin production, pH tolerance, or metabolic versatility) that were not measured. The conclusion that \"resident community properties are the primary factors\" requires ruling out invader identity effects more rigorously than by examining only monoculture growth characteristics. The concentration of successful invasions in specific invader taxa suggests that unexamined invader traits likely contribute substantially to invasion outcomes.\n\nReferences:\n[7] Williamson MH & Fitter A (1996). The characters of successful invaders. *Biological Conservation* 78: 163-170. https://doi.org/10.1016/0006-3207(96)00025-0", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Claude|5", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "Communities are classified as \"fluctuating\" or \"stable\" based on a biomass standard deviation threshold of 0.05, which appears to be chosen without rigorous statistical justification, and all low-nutrient communities are automatically classified as stable regardless of their actual dynamics.\n\n\"The standard deviation of community biomass over day 5, day 6 and day 7 show that the stability threshold of 0.05 can separate the communities into stable ones (purple points) with small biomass deviation and fluctuating ones (orange points) with relatively large biomass deviation under high nutrient.\"\nThe threshold value of 0.05 for standard deviation appears to be set based on visual inspection of the data distribution rather than a principled statistical criterion. The classification uses only 3 time points (days 5-7) to characterize community dynamics, which provides limited information about true dynamical states. Distinguishing between genuine ecological fluctuations and measurement noise requires more rigorous methods, such as testing for autocorrelation or using statistical models to classify time series [[8]](#citation-list).\n\"The standard deviation of community biomass under low nutrient are small (all below the stability threshold of 0.05), which were naturally classified into stable communities.\"\nThe automatic classification of all low-nutrient communities as \"stable\" based solely on the threshold being chosen from high-nutrient data represents circular reasoning. If the threshold were set differently, some low-nutrient communities might be reclassified, potentially altering the conclusions about how interaction strength affects stability and invasibility. The paper does not explore how sensitive the results are to the choice of this threshold value.\n\"8 out of the 17 resident communities reach fluctuation in biomass (orange) and the rest 9 communities reach stable states (purple).\"\nThe nearly even split between fluctuating (8) and stable (9) communities raises the question of whether the threshold was chosen post-hoc to achieve a particular balance. A rigorous approach would involve pre-registration of the threshold criterion or use of an objective method (e.g., model-based classification of dynamical regimes) to categorize communities. Additionally, with only 8-9 communities in each category, subgroup analyses comparing invasion rates have very limited statistical power, as demonstrated by the wide confidence intervals around estimated invasion probabilities.\n\nReferences:\n[8] Hu J, Amor DR, Barbier M, Bunin G & Gore J (2022). Emergent phases of ecological diversity and dynamics mapped in microcosms. *Science* 378: 85-89. https://doi.org/10.1126/science.abm7841", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|GPT|1", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "This paper makes an overgeneralized claim (Validity; Conclusions) that invasion probability universally collapses onto survival fraction across conditions, but the main theoretical support relies on an exchangeable generalized Lotka–Volterra setup (identical intrinsic parameters and randomly drawn interactions) that can mechanically enforce such a collapse, and the experiments do not establish universality beyond the studied library and protocol.\n\n“Despite these conflicting diversity-invasibility relationships, after scaling richness with species pool size to get the survival fraction, we found that all communities collapsed to a universal line in which the invasion probability is approximately equal to the survival fraction (Fig. 4b).”\nThis sentence asserts a universal relationship, but the paper’s own phrasing indicates the collapse is obtained after a specific rescaling (richness divided by pool size), not from an independently validated mechanism. A collapse can occur for multiple reasons, including shared definitions and exchangeability assumptions, without implying universality across ecological contexts. The manuscript does not provide out-of-distribution validation (e.g., different taxa, interaction types, or invasion protocols) to justify the “universal” framing. Because later conclusions extrapolate this relationship to natural communities, the evidentiary standard should be higher than a within-system collapse. The paper would need clearer limits on scope (e.g., “within these assembled microcosms and this dispersal/invasion protocol”) or additional tests demonstrating the relationship persists under qualitatively different invasion settings.\n“For simplicity and without qualitatively changing our results, we considered the same growth rate \\( r_i = 1 \\) and the same carrying capacity \\( K_i = 1 \\) for all species in the main text.”\nSetting all intrinsic growth rates and carrying capacities equal makes species effectively exchangeable except through the random interaction matrix, which strengthens symmetry-based relationships between resident survival and a “new” species’ invasion probability. Under such exchangeability, the probability that an added species persists can become tightly linked to the fraction of species that persist from the same parameter distribution. This means the reported collapse may partially reflect model construction rather than an empirically grounded ecological law. The manuscript does not quantify how sensitive the claimed universality is to realistic heterogeneity in \\(r_i\\), \\(K_i\\), or interaction structure beyond citing prior work. Given that microbial interactions are often mediated by environmental modification and can be strongly context-dependent, these simplifications matter for the validity of universal claims. At minimum, the paper should show the collapse persists under broader, empirically motivated parameter heterogeneity and/or mechanistic mediation.\n```matlab\nr = ones(S, 1); % Growth rates (set to 1 for simplicity)\nAA = rand(S, S)*A*2;\nAA = AA - diag(diag(AA)) + eye(S); % Ensure diagonal elements are 1\n...\nAA(S, :) = (rand(1, S) + 0.5) * A;\nAA(:, S) = (rand(S, 1) + 0.5) * A;\n```\nThis code implements the exchangeability noted in the text: identical intrinsic growth rates and a randomly sampled interaction matrix for all species, including the invader. The invader’s interaction coefficients are drawn from the same strength scale \\(A\\) as the residents, which makes “invader vs resident” a label rather than a qualitatively different ecological role. In such a setup, it is unsurprising that invasion success statistics can align with resident survival statistics, because both are governed by the same parameter-generating process. This weakens the interpretation that a collapse reveals a universal, community-level predictor rather than a consequence of how the model was parameterized. If the paper’s universality claim is meant to apply to real invasions (often involving species with systematically different traits or interaction mechanisms), the model should test non-exchangeable invaders (e.g., shifted \\(r\\), \\(K\\), or interaction distributions). Without that, the link between the modeled collapse and the empirical “universal” claim remains under-justified.\n“Pairwise models are commonly used to describe many-species communities. In these models, an individual receives additive fitness effects from pairwise interactions with each species in the community ('additivity assumption'). All pairwise interactions are typically represented by a single equation where parameters reflect signs and strengths of fitness effects ('universality assumption'). Here, we show that a single equation fails to qualitatively capture diverse pairwise microbial interactions.” ([1](#ref1))\nThis external evidence highlights a known limitation of relying on a single Lotka–Volterra-type pairwise equation form as a universal description for microbial interactions. The reviewed paper’s “universal correspondence” is derived in large part from such a gLV framework, while the experiments themselves involve media modification (e.g., pH) and dispersal that can create higher-order or mediated effects. If gLV’s universality/additivity assumptions fail in many microbial settings, then a “universal” law inferred from gLV requires extra empirical validation rather than being taken as broadly applicable. The manuscript does not directly address whether the mechanisms generating its experimental priority effects and fluctuations are compatible with pairwise-additive gLV dynamics in the relevant regimes. This undermines the strength of conclusions that elevate a model-derived collapse to a general predictive principle. A stronger approach would triangulate with mechanistic mediation models or demonstrate that inferred pairwise dynamics accurately predict unseen invasion scenarios.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "The paper utilizes a fundamentally incorrect implementation of the Runge-Kutta 4th order (RK4) method for simulating the generalized Lotka-Volterra (gLV) model, effectively reducing the order of accuracy for the interaction terms to that of a first-order Euler method.\n\n```matlab\nk1 = r(j) * NN(i-1, j) * (1 - AA(j, :) * (NN(i-1, :)')) * step;\nk2 = r(j) * (NN(i-1, j) + k1 / 2) * (1 - AA(j, :) * (NN(i-1, :)')) * step;\nk3 = r(j) * (NN(i-1, j) + k2 / 2) * (1 - AA(j, :) * (NN(i-1, :)')) * step;\nk4 = r(j) * (NN(i-1, j) + k3) * (1 - AA(j, :) * (NN(i-1, :)')) * step;\nNN(i, j) = NN(i-1, j) + (1/6) * (k1 + 2*k2 + 2*k3 + k4);\n```\nIn a correct RK4 implementation for a system of coupled differential equations, the interaction terms (which depend on the abundances of other species) must be updated at each intermediate step (k2, k3, k4) using the estimated intermediate states of all species. The provided code calculates `k2`, `k3`, and `k4` for species `j` using `NN(i-1, :)` (the state at the beginning of the time step) for the interaction term `(1 - AA(j, :) * (NN(i-1, :)'))`. This treats the interaction effects from other species as constant across the time step, which is characteristic of a first-order Euler method or a splitting method, not a fourth-order method.\n\"We simulated the dynamics of communities... to show that, taken together, they explain many features of invasibility and invasion effects.\"\nThe paper relies heavily on these simulations to characterize \"dynamical regimes,\" including chaotic or fluctuating states which are known to be highly sensitive to numerical errors [1]. Using a low-order integration scheme for coupled non-linear dynamics can lead to significant errors in trajectory, stability analysis, and the classification of dynamical regimes, thereby undermining the theoretical conclusions of the paper.\n\nReferences:\n[1] Butcher, J. C. (2016). Numerical methods for ordinary differential equations. John Wiley & Sons.", "reviewer_type": "ai", "label": "error", "error_type": "Unstated statement", "label_origin": "expert+llm-filter"}
{"id": "prb|28|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "The claim that \"emergent priority effects\" explain the reduced invasibility in high-nutrient communities is speculative and not supported by direct experimental evidence of history dependence.\n\n\"We interpret the mismatch between invasion probability and survival fraction under high nutrient as evidence of priority effects in the community assembly under strong interactions in our experiment.\"\nThe authors infer priority effects solely from the observation that invasion probability is lower than the survival fraction of the resident community. However, this \"mismatch\" could simply result from the resident community being competitively superior or more resistant due to other factors (e.g., niche preemption) without any history dependence.\n\"In ecology, the priority effect refers to the phenomenon in which the community structure is influenced by the order and timing of species’ arrival in a community\"\nAs defined, priority effects require demonstrating that the outcome depends on arrival order [3]. The authors only tested one sequence (resident assembly followed by invasion). To claim priority effects, they would need to show that the invader could establish or dominate if it had arrived earlier or at the same time as the residents. Without such counterfactual experiments, the \"priority effect\" remains an unverified hypothesis.\n\nReferences:\n[3] Debray, R., Herbert, R. A., Jaffe, A. L., Crits-Christoph, A., Power, M. E., & Koskella, B. (2022). Priority effects in microbiome assembly. Nature Reviews Microbiology, 20(2), 109-121. https://doi.org/10.1038/s41579-021-00604-w", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "The paper claims a \"universal positive correspondence\" between invasibility and survival fraction, yet its own data shows significant systematic deviations from this relationship in the high-nutrient regime, contradicting the claim of universality.\n\n\"Our results... showing a universal positive correspondence between invasibility and survival fraction of resident species across all conditions.\"\nThe term \"universal\" implies a relationship that holds across the tested domain. However, the authors explicitly note that this is not the case for their most distinct experimental condition.\n\"majority of points on the bottom left (high nutrient) are below the diagonal line... mismatch between invasion probability and survival fraction\"\nThe high-nutrient communities (representing the \"strong interaction\" regime) systematically fall below the predicted line, showing significantly lower invasibility than predicted by survival fraction. This systematic deviation indicates that the survival fraction is not a \"universal\" predictor but rather a correlate that breaks down exactly in the regime of interest (strong interactions), which the authors attempt to explain away with the unverified \"priority effect\" hypothesis.", "reviewer_type": "ai", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|28|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "My first main comment concerns the exposition of the different diversity-invasibility relationships between Fig. 1 and Fig. 2/3, which on a first read was not immediately obvious. In Fig 1, more species and higher interaction strength makes for fluctuations and greater diversity, and fluctuating communities are more likely to be invaded; but both theory and Fig. 3 show a negative correlation between invasion probability and pool size/interaction strength. I naively expected increased pool size and stronger interactions to translate to a higher change of fluctuations (as in their recent paper), and thus greater richness and higher invasion probability. It is later revealed where this apparent contradiction comes from, but I believe it would be immensely helpful if this contradiction was highlighted early on. This issue is made more severe by the use of three different terms to describe the probability of successful invasions (invasion probability and invasion resistance, also invasibility) – especially because these have opposite meanings, I had to read this section of the manuscript carefully to understand its meaning. A single term would be easier to understand.", "reviewer_type": "human", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|28|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "My second main comment concerns the notion of priority effects. Here, as I understand it, the authors use this term basically to mean that a community of strongly interacting species has established itself, which makes invasions less likely (e.g., because all niches are filled or because antagonistic interactions are balanced out) but I am not convinced that this is the sense in which most ecologists tend to use that term; to me, the more common use appears to be referring to particular species whose presence or absence steers the community into different alternative stable states. Here, however, the community is already in a stable state and a new species is trying to invade, and thus “priority effect” does not apply in my view. I suggest a different way of describing this effect here, or, at the very least, the sentence in line 244-246 needs more explanation. Similarly, I find the use of “alternative stable states” (l251) to be unclear since that is not really the subject of this paper.", "reviewer_type": "human", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|28|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "L110: “The lower probability” -- compared to what?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "L227: correlation on -> with", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "L280: ergodicity likely needs a bit more explanation to be clear", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "L285: definition of invasion effect is slightly unclear. Is this the same definition as in L296?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_1|10", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "Fig 2f/4c: Legend missing for the gray lines", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_1|11", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "Fig 4a: it is very hard to parse the different colors", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "My understanding is that the term “fluctuations” in the context of this study means fluctuations induced by chaotic dynamics. I understand that these are not meant to be viewed as stochastic fluctuations, but in my experience, I have found that only a fraction of eco/evo readers understand the distinction between fluctuations induced by deterministic vs. stochastic effects. It would aid the typical reader if the authors clarified what form of fluctuations they are focused on in the Introduction, specified the type of fluctuation whenever the term is used in the manuscript (e.g., “fluctuations” “deterministic fluctuations”), and briefly addressed in the Discussion how the consideration of stochastic fluctuations might factor into their subsequent research efforts.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "It is worth briefly mentioning in the supplement why continued migration from the regional pool was a necessarily experimental detail for this study. Specifically, how the absence of experimentally-imposed migration would correspond to a gLV with zero migration, the analytic results of which would be decidedly less rich (e.g., no chaos, etc.). Broad readership may not pick up on this detail.\\n\\nRelated, did the authors perform any experiments without daily migration from the regional pool? Contrasting the results of this study with that type of experiment would strengthen their claims and provide further opportunities to test the utility of the gLV. Alternatively, if there are any published experiments on invasion analysis using a similar experimental setting without imposing migration, then such results could be verbally compared to the results of their experiment.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "Is the experimentally-imposed migration rate sufficient to induce chaotic dynamics in the context of their gLV model? I searched for this detail in the supplement but did not find it.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "I would also encourage the authors to make both their code and raw data available on public repositories to ensure transparency and reproducibility.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "Lines 148-149: It would help the reader if justification for the extinction threshold was provided in the main text. In lines 81-82 of the supplement the authors describe the lower bound on detection due to sequencing, but it is not clear how they arrived at this particular value. It would also help if there was a comparison between the chosen threshold and the inverse of the typical total abundance of the community (all cells), the threshold for true extinction, to provide context for the detection limitation.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "Lines 208-211: I am unaware of models where the competition coefficients between species can be examined as a function of media modification. If such a model exists, could the authors briefly describe it in their supplement to help the reader understand how environmental variables (e.g., pH) map onto competition coefficients in a gLV model?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "Lines 275-280: How are alternative stable states determined here?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "Fig. 1d: Why are all but two of the “fluctuating” communities decreasing in biomass from day four to five. Could this simultaneous decrease in biomass be driven by experimental details rather than by the intrinsic dynamics of the communities?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_2|10", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "Fig. 1g; lines 380-382: What statistical test was performed here?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_2|11", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "Fig. 2f: What do the dashed and solid grey lines represent? Could the authors include a legend in the figure?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_2|12", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "Fig. 4c: Could the authors add an axis label for the colorbar in the revision?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_2|13", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "Fig. 4d: “Effect on resident community” is a nice term for those unfamiliar with these types of experiments, but it still reads as somewhat vague. Could the authors describe what this term means in the figure legend and provide an equation for how the quantity was estimated in the supplement?", "reviewer_type": "human", "label": "error", "error_type": "Neglect", "label_origin": "expert+llm-filter"}
{"id": "prb|28|Human_2|14", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "Fig. 5: What timepoints are used to calculate the fold change? Are the same timepoints used for each community? Is the outcome of the statistical test robust to the choice of timepoints?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_2|15", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "Supplement line 52: The sampling detection limit is ~10^{4}(-4)but the chosen dilution rate was 10^{4}(-5). How does the difference between dilution rates and detection limit shape the observed outcomes of the experiment? If it does, it may be worth describing the outcomes in different parameter limits to the reader (i.e., sampling limit much greater than dilution rate and vice-versa).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_2|16", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "Supplement: Lines 52, 63: I am unfamiliar with the term “dispersal rate” used to describe the process of diluting cultures in a serial transfer experiment. The method used by the authors is different from the standard process of serial dilution, so I think some justification of the term as well as an explanation of how it connects to the mathematical definition of dispersal (Eq. S1) in the supplement is warranted.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_2|17", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "Supplement lines 100-119: Does the absence of serial dilution being explicitly encoded into the simulation impact the results? Serial dilutions have been explicitly incorporated into mechanistic (Marsland et al., 2020) and phenomenological (Shoemaker et al., 2023) models of community dynamics in an experimental context. Could the authors provide justification of why serial dilution does not need to be explicitly encoded into their simulation?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_2|18", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "Supplement lines 109-111: What are the units of time and how do they compare to the timescales of the experiments? Is the timescale of the simulation informed by the timescale of the experiment?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_2|19", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "Supplement lines 147-148: It’s unclear what the CV represents. My understanding is that each CV is calculated over time for each species for a given simulation iteration. Since the dynamics are deterministic and the interaction coefficients are a form of quenched disorder, what random variable is the CV calculated over? Does the distribution of CVs demonstrate a clear bimodality with the 10^{4}(-3) cutoff representing the valley between the two peaks? It would help the reader if 1) additional context was provided for the CV and what it represents as well as 2) distributions of simulated CVs plotted to demonstrate the intuition behind classifying communities into stable/fluctuating classes.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_2|20", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "Supplement lines 160-163, Fig. S12c, d: Is some degree of correlation expected since biomass was used to calculate the abundance of each species? This seems similar to the case presented in. Garud et al., where the same parameter factors into both sides of the relationship (pg. 16 and 17 of supplement; 2019). Here the authors partitioned synonymous sites into two categories, providing two estimates of the quantities of interest. These two quantities are conditionally independent of the parameter that factors into both sides of the proposed relationship due to the Poisson thinning property. One quantity is then used to calculate the left side of the relationship while the other is used to calculate the right side. Is a similar analysis appropriate in this case given that total biomass factors into both sides of the quantities examined in Fig. S12c, d?\\n\\nAn alternative option could be to examine the relationship between the CV of biomass (OD) and the CV of relative abundances for each ASV, allowing for the identification of community members that disproportionately contribute to the fluctuations in biomass.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_2|21", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "Fig. S2: Is there any phylogenetic structure to these results? Does the placement of a species on the phylogeny relative to the phylogenetic composition of a given community determine species invariability?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_2|22", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "Fig. S12: “The standard deviation of community biomass over day 5, day 6 and day 7” this detail is confusing since the timeseries represented in Fig. 1d ends at day six. What was the rational behind using only these three timepoints? Some justification of using these three timepoints is needed in the Supplement.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_2|23", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "Fig. S13: The figure is a useful visualization, but in its current form it is difficult to validate the claims made in the legend.\\n\\n- “Invisibility positively correlates with richness when varying interaction strength” Is a claim being made here about the direction in which the correlation changes with a change in interaction strength? It’s not clear to me whether this claim is about the existence of positive correlations among treatments or the difference in positive correlations between treatments.\\n\\n- “Invisibility positively correlates with richness when randomly sample S=20 communities under high nutrient, due to fluctuating communities display larger richness and larger invasion probability.” I am having a hard time parsing this statement. Is a claim being made about correlation being higher in high nutrient S=20 fluctuating communities relative to high nutrient S=20 stable communities?\\n\\n- The legend could use some retooling for clarity. Furthermore, if the claims are about the increase in correlation in one treatment vs. another, then additional statistical analyses are necessary. It seems like the authors are making three claims, which would require three tests. The question is what statistical model to use. A full regression analysis to examine the increase in slope between two treatments while controlling for potential cofounders could be seen as necessary. Alternatively, the authors could test for the difference between two correlation coefficients using Fisher’s Z statistic with a null distribution obtained by permuting community identity for a given pair of treatments (Snedecor & Cochran, 1989). This statistic was recently used to test for the change in correlation coefficients in experimental microbial communities (Eq. 21 in Shoemaker et al., 2023).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_2|24", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "Fig. S15, S16: Some type of statistical test is necessary to establish the claim that invasions lead to changes in community composition. There are multiple ways to accomplish this task and the authors may have their own idea. One immediate option strikes me: calculate a paired t-statistic for each community between the control and successfully invaded community, demonstrating that absolute value of the t-statistics is significantly greater than zero. Null distributions could be obtained by permuting control/invade labels of each species within each community.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_2|25", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "Fig. S17, S18: Similar to Fig. S15 and S16, but now there are different invader species for each community. The authors could perform a paired t-test for each invader species, pooling observations across communities. A null could be generated for each invader species by permuting control/invade labels within each species within each community.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_2|26", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "Figs. S15-S18: Is there any relationship between the relative abundance of the invading species and the change in relative abundance of the remaining species between the control/invade treatments? This may not be the most appropriate analysis for compositional data, but you plot the relative abundance of the invading species vs. the mean difference in relative abundance between treatments for the remaining species, do you see a clear relationship?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_2|27", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "Fig. S19-S21: The authors’ claims about the lack of correlations appear correct but I think the correlation coefficient should be provided along with the non-significant P-value. Statistical significance can be assessed by permuting x and y vectors. Permutations should be constrained on species identity for Fig. S19.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "The authors state that increasing interaction strength decreases invasion probability. This is done experimentally by increasing the strength of competitive interactions. However, previous work (ref 30) has demonstrated that the type of interaction between the invader/residents, or between residents, impacts the invasion outcome. For example, positive interactions (e.g. facilitation) between the invader and resident community increases invasion probability (as posited by the diversity begets diversity hypothesis). Increasing interaction strength in this case could increase community invasibility, which is a possibility not considered by this study. While I recognise that experimental manipulation of interaction strength is difficult, I would recommend running the model with a distribution of interactions that considers positive interactions, to show the generality of their conclusions. If this has already been done (this is not clear) this should be included in the supplement.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "The limitations of the study in determining the impact of successful invasions on the structure of the resident community should be more explicit. The impact of successful invasions on the structure of the resident community was measured experimentally by the fold change in biomass, and the invasion effect on the community using 16s sequencing data. However, the fold change in biomass provides little insight on invasion impact. It is not possible to distinguish between the change in biomass of the resident community, and the increase in biomass of the successful invader. Thus, a lower change in biomass in the low nutrient regime may be due to the fact that the invader has less nutrients to grow on, and the converse for the high nutrient regime. Moreover, while species abundance data shows a statistically significant difference in community composition in the higher nutrient regime, it is important that the authors provide information about the effect size. For example, as a 95% confidence interval for the difference between the invasion success under high nutrient conditions and the invasion success under low nutrient conditions Finally, it is hard to conclude what the actual effect of invasion is using the selected measures. For example, though species composition may have changed, the invader could be functionally redundant with the species that were excluded, resulting in no change to community functioning. While a comprehensive assessment of invasion impact is out of the scope of this paper, I would recommend for these limitations to be discussed explicitly in the manuscript.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "I strongly recommend including explicit definitions of key terms, which would improve clarity of the manuscript. For example, the definition of community diversity as the number of species that survive the assembly process is not made explicit in line 152. What 'rich dynamics' (line 191) or richness (line 195, 222 and others) refers to is also unclear to me.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "The findings of this study could be embedded more explicitly into existing concepts in invasion ecology, which is dominated by niche theory and resource competition. For example, in lines 175-176 the authors state that fluctuating communities are more invasible. The basis of this relationship is not made clear to the reader - I assumed that this means more niches are open at any given point in time. Moreover, why strong interspecies interactions and a larger species pool decrease invasibility is not discussed. It would also be helpful to discuss this more in the conclusion.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "I think that for those unfamiliar with previous work from this group, how interaction strength, species pool size and dynamical regime combine to determine survival fraction is difficult to understand. More explanation about how these features interface is necessary for clarity of the manuscript, since they are not independent. For example, it is not immediately clear why there are stable/fluctuating regimes for communities under high nutrient conditions, and not for low nutrient conditions", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "The measure of dispersion used is not included in the text of the manuscript (i.e., on line 148, 153, 154, 172 and more, parameter estimates are given as mean +/- X, where X is a measure of dispersion, but which measure it is is not defined). Defining the measure of dispersion is crucial to allow for interpretation of the findings. Some figure legends mention that error bars represent the standard error of the mean, which I assume is the measure used by the authors, but this should be clearly stated in the text of the manuscript.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_3|7", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "State how invaders were chosen (line 146) - I assume they were chosen at random?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_3|8", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "In the section discussing the model (lines 178-190), explicitly state at what relative abundance the invader is introduced relative to the community", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|28|Human_3|10", "source": "prb", "split": "test", "paper_id": "prb28", "comment": "I would include (strong interaction) or (weak interaction) every time high/low nutrient conditions are mentioned for clarity. This is missing now in line 240 and others", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|29|Claude|1", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "The paper develops and validates predictive models using in vitro stool-derived microbial communities that completely lack host immune components known to be essential mediators of colonization resistance. This fundamentally limits the translational relevance of the findings to actual human gut colonization.\n\n\"To systematically study colonization outcomes in complex microbial communities, we established large-scale cultivation of human stool-derived in vitro communities in multi-well plates\"\nThe in vitro experimental system captures only microbe-microbe interactions and lacks the host compartment entirely. This is a substantial simplification because colonization resistance in vivo involves bidirectional host-microbiota interactions that cannot be recapitulated in a static fermentation system.\n\"Our results suggest that the colonization resistance of microbial communities is predictable and tunable via the data-driven approach\"\nThis conclusion overstates the applicability of the findings. The predictability demonstrated pertains to in vitro systems where only microbial competition matters, but extrapolating this to claims about \"microbial communities\" broadly (including in vivo scenarios) is not warranted given the experimental design.\n\"Colonization resistance is a fundamental host defense mechanism that relies on the synergistic interaction between the gut microbiota and the host immune system to prevent enteric pathogen colonization and infection... The gut microbiota provides direct protection by occupying ecological niches, competing for nutrients, producing bacteriocins and engaging in contact-dependent inhibition... The host contributes through physical and chemical mucosal barriers as well as innate and adaptive immune responses.\" from [Li & Guo (2025)][1]\nRecent literature explicitly establishes that colonization resistance requires both microbial and host immune components working synergistically. The in vitro system used in the paper captures only the microbiota component while entirely missing the host immunity component, which includes IL-22-mediated antimicrobial peptide production, epithelial glycosylation, secretory IgA, and mucus barrier dynamics—all known to shape colonization outcomes.\n\"ILC3 deficiency increased epithelial galactosylation, facilitating overgrowth of the mucin-degrader A. muciniphila... This reveals that ILC3-derived IL-22 controls broader glycosylation patterns that shape microbial community structure and pathogen behavior.\" from [Li & Guo (2025)][1]\nA. muciniphila, one of the two invading species tested in the paper, is specifically regulated by ILC3-IL-22 host pathways through epithelial glycosylation. The in vitro system cannot capture these dynamics, yet the paper draws conclusions about A. muciniphila colonization predictability that may not translate to in vivo contexts where host immune regulation plays a role.\n\nReferences:\n[1] Li, N. & Guo, X. (2025). The gut microbiota and host immunity synergistically orchestrate colonization resistance. *Gut Microbes*. https://pmc.ncbi.nlm.nih.gov/articles/PMC12773493/", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|29|Claude|2", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "The PERMANOVA analysis shows that baseline community composition explains only 2-3% of variance in colonization outcomes (R² = 0.03 for E. faecium, R² = 0.022 for A. muciniphila), yet the paper claims that colonization outcomes are \"predictable\" from baseline composition with AUROC values of 0.86. This apparent contradiction is not adequately addressed, raising questions about what the machine learning models are actually capturing and whether the baseline composition alone drives the observed classification performance.\n\n\"Principal component analysis (PCoA) based on the Bray-Curtis dissimilarity of the compositional profiles of baseline communities. The difference between permissive and resistant communities was significant (PERMANOVA Adonis test, R² = 0.03, p < 0.0001)\"\nAn R² of 0.03 indicates that baseline community composition explains only 3% of the variance between permissive and resistant communities for E. faecium colonization. While statistical significance was achieved (p < 0.0001), the effect size is notably small. Standard interpretations suggest that R² below 0.1 indicates weak relationships.\n\"The difference between highly permissive and lowly permissive communities was significant (PERMANOVA Adonis test, R² = 0.022, p < 0.001)\"\nSimilarly, for A. muciniphila, the baseline composition explains only 2.2% of variance between high and low permissive communities. Such small effect sizes suggest that factors other than community composition contribute substantially to colonization outcomes.\n\"Random Forest classifier displayed the best performance in predicting whether E. faecium could successfully colonize based on the species-level community composition (AUROC=0.86)\"\nThe paper reports high classification performance (AUROC=0.86) while the PERMANOVA R² is only 0.03. While these metrics measure different aspects—AUROC measures discrimination ability while R² measures variance explained—the stark difference warrants discussion. High AUROC with low R² can occur when there are subtle but consistent differences between groups; however, this means the models may rely on small marginal differences that could be sensitive to technical variation or may not reflect ecologically meaningful predictors.\n\"Grazing clearly affects community composition, though it accounts for a relatively small amount of the variation in composition (5.6%).\" from [Applied Multivariate Statistics in R - PERMANOVA chapter][2]\nStandard interpretation in ecological studies considers R² values around 5-6% as explaining \"a relatively small amount\" of variation. The R² values in this paper (2-3%) are even smaller, yet are used to support conclusions about predictability without acknowledging this limitation.\n\nReferences:\n[2] Applied Multivariate Statistics in R - PERMANOVA. https://uw.pressbooks.pub/appliedmultivariatestatistics/chapter/permanova/", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|29|Claude|3", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "The synthetic data validation uses the Generalized Lotka-Volterra (GLV) model, for which the authors derive an analytical linear relation between baseline composition and post-invasion abundance (achieving Spearman ρ = 1.0). This creates an idealized scenario where the ground truth has a known linear structure. The paper acknowledges this linear relation \"doesn't hold for other dynamical models\" yet uses this validation to support broader claims about the data-driven approach's applicability to real biological systems with unknown, likely non-linear dynamics.\n\n\"The analytically derived relation can fully explain the simulated colonization outcomes in GLV model (Fig.S1, Spearman correlation ρ = 1, p < 0.001)\"\nWhen the analytical derivation produces a perfect correlation (ρ = 1) with simulated data, this means the synthetic validation is essentially testing whether machine learning can learn a known linear relationship. This is a much easier task than learning from real biological systems where the underlying dynamics are unknown and likely non-linear.\n\"Although the linear relation doesn't hold for other dynamical models, it suggests that learning the mapping for COP is feasible by the data-driven approach\"\nThe paper explicitly acknowledges the limitation that the linear relation is specific to GLV dynamics, yet extrapolates from this to claim feasibility for the general data-driven approach. This logical leap is problematic because real microbial communities may follow dynamics with higher-order interactions, metabolic cross-feeding, and other non-linear processes that violate the GLV assumptions.\n\"We generated synthetic data of colonization outcomes using the Generalized Lotka-Volterra (GLV) model\"\nThe GLV model assumes pairwise linear interactions and lacks higher-order interactions, metabolic modeling, or spatiotemporal dynamics present in real gut communities. While GLV is a reasonable starting point, using perfect GLV fit as primary validation may overestimate the approach's effectiveness in more complex real-world scenarios.\n\"Coexistence in diverse communities with higher-order interactions... In the generalization of the Lotka–Volterra model we consider, every species has an abundance that is fixed by its intrinsic growth rate and its self-regulation\" from [Gibbs et al. (2022)][3]\nRecent ecological modeling literature has demonstrated that higher-order interactions play important roles in community dynamics and coexistence that are not captured by standard GLV models. By validating on GLV synthetic data, the paper tests an idealized scenario that may not reflect the complexity of real microbial communities.\n\nReferences:\n[3] Gibbs, T., et al. (2022). Coexistence in diverse communities with higher-order interactions. *PNAS*, 119(43), e2205063119. https://www.pnas.org/doi/10.1073/pnas.2205063119", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|29|Claude|4", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "The experimental validation tests only two invading species (E. faecium and A. muciniphila), both of which have specific ecological niches and characteristics. E. faecium is a facultative anaerobe that can tolerate harsh conditions, while A. muciniphila is a specialized mucin degrader. The generalizability of the data-driven approach to other invading species with different ecological strategies remains untested.\n\n\"We conducted colonization experiments for two commensal gut bacteria species Enterococcus faecium and Akkermansia muciniphila in hundreds of human stool-derived in vitro microbial communities\"\nTesting only two species limits the ability to make general claims about the data-driven approach for predicting colonization outcomes. Different invading species may rely on different ecological mechanisms (nutrient competition, antimicrobial production, niche occupation) that could require different features for prediction.\n\"We conducted a preliminary experiment to investigate the colonization outcome of different exogenous species (Fig.S5). We found that E. faecium, A. muciniphila, and F. nucleatum could successfully colonize in some communities... In contrast, S. salivarius, B. breve, and Lactobacillus spp. could not colonize in nearly all the communities we tested\"\nThe preliminary experiments show that different species have very different colonization abilities. The fact that several species (S. salivarius, B. breve, Lactobacillus spp.) could not colonize any communities means the machine learning approach was not tested for these species. Species-specific biological factors may determine colonization success in ways that are not generalizable across taxa.\n\"A. muciniphila... is a specialized mucin-degrader... ILC3-derived IL-22 controls broader glycosylation patterns that shape microbial community structure and pathogen behavior\" from [Li & Guo (2025)][1]\nA. muciniphila's ecological niche as a mucin degrader makes it unique among gut bacteria. In the in vitro system lacking mucin dynamics regulated by host signals, the factors determining A. muciniphila colonization may differ substantially from in vivo scenarios. This limits the extent to which findings about A. muciniphila colonization prediction can be generalized.\n\nReferences:\n[1] Li, N. & Guo, X. (2025). The gut microbiota and host immunity synergistically orchestrate colonization resistance. *Gut Microbes*. https://pmc.ncbi.nlm.nih.gov/articles/PMC12773493/", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|29|Claude|5", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "The \"colonization impact\" analysis, which identifies species that influence invasion outcomes, is based on perturbing trained machine learning models rather than direct experimental measurements. While the E. faecalis-E. faecium interaction was validated experimentally, the colonization impacts for most other species remain model-based inferences that could reflect artifacts of the training data or model architecture rather than genuine biological interactions.\n\n\"To compute the colonization impact, i.e., the impact of a resident species on the colonization outcome of the invading species, we first trained the prediction models using all the samples. Then, we performed a thought experiment by introducing a perturbation in the abundance of the resident species\"\nThe colonization impact metric is derived from model predictions under simulated perturbations rather than actual experimental perturbations. This approach assumes that the trained model accurately captures the causal relationships between resident species and colonization outcomes, which may not be the case if the model is fitting correlational patterns.\n\"In comparison, Clostridium symbiosum, a species predicted to have a neutral impact, did not alter the colonization of E. faecium\"\nThe experimental validation tests only one positive case (E. faecalis inhibits E. faecium) and one negative control (C. symbiosum is neutral). The paper identifies multiple species with predicted strong colonization impacts (Figure 5D-G shows rankings of many species) but only one interaction is validated, leaving the accuracy of the other predictions unknown.\n\"The median colonization impact of a resident species across different local communities was positively correlated to its interaction strength on the exogenous species (Spearman correlation coefficient ρ = 0.73)\"\nThis correlation is derived from synthetic GLV data where interaction strengths are known by construction. In real experimental data, the true interaction strengths are unknown, so the claim that colonization impact reflects genuine ecological interactions cannot be directly verified beyond the single E. faecalis validation.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|29|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "The paper claims to \"infer the impact of each resident species\" using the machine learning model, but this inference is based on model sensitivity analysis and lacks comprehensive experimental validation.\n\n\"Learning the mapping from the baseline taxonomic profile to colonization outcomes can help us infer the impact of each resident species on the colonization of the exogenous species\"\nThe authors use a \"thought experiment\" (perturbation analysis) on the trained model to infer interactions. While this reveals what the *model* uses for prediction, it does not necessarily reflect true ecological interactions, as machine learning models (especially Random Forest) can rely on correlated features rather than causal drivers.\n\"strongly interacting species could significantly alter the colonization outcomes, e.g., the presence of Enterococcus faecalis inhibits the invasion of E. faecium.\"\nThe authors validate this specific interaction (Fig. 3D, Fig. S16), but they do not validate the broader set of inferred interactions. Without broader validation (e.g., using mono-colonization or pairwise assays as in [2]), the claim that the method can reliably \"infer the impact of each resident species\" is overreached. The method generates hypotheses, but the \"inferred impact\" should not be equated with confirmed ecological interaction without further proof.\n\nReferences:\n[2] Weiss, A. S. et al. In vitro interaction network of a synthetic gut bacterial community. ISME J 16, 1095-1109 (2022). https://www.nature.com/articles/s41396-021-01153-z", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|29|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "The stool communities are treated with 12 different antibiotics. Thus, the authors cannot describe communities as permissive or resistant since it is not clear whether the community composition per se or the antibiotic treatment hampered colonisation. In this context, we need to know how sensitive E. faecium and A. muciniphila are to the 12 antibiotics tested. Perhaps this sensitivity is as good as or even a better predictor of invasion success than the composition of the target communities. If this turns out to be the case, the entire point of this study is undermined and the authors would need to demonstrate that machine learning approaches can predict invasion success on untreated stool samples.", "reviewer_type": "human", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|29|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "L. 338-340: \\\"We demonstrate that the data-driven approach enables accurate function prediction and system-level understanding of complex microbial communities.\\\" This is a big claim. Which systems-level understanding did the authors gain? They did not learn the mechanism behind the interaction between E. faecalis and E. faecium. The advantage of knowing mechanisms is that the model is better able to deal with changes in conditions, such as lower pH or different nutrient levels. A machine learning approach may work in a given situation but will have to be retrained when circumstances, such as the medium, change. This weakness of the data-driven approach is not discussed.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|29|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "The gLV simulations deviate from the real case in an important point: the exogenous species may have been already present in the stool communities, perhaps below detection level. In that case, not the colonisation itself is of interest but the boost given to the \\\"exogenous\\\" species (which may be due to some density-dependent mechanism). This issue needs to be discussed. Another problem is that no noise was added to the simulated data. However, sequencing comes with large technical variation, so it is important to assess the robustness of the machine learning tools to such variation.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|29|Human_1|10", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "Another limitation to be discussed is the presence of mucin in liquid form. I assume this was necessary to enable the growth of A. muciniphila, but it deviates from the biology of the intestinal system, where A. muciniphila prefers to colonise (solid) mucin and other gut bacteria prefer the lumen. It would be of interest to find out to what extent A. muciniphila's ability to colonise the tested communities depends on the mucin concentration in the medium.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|29|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "To what extent maybe simpler statistical models (including LASSO regression) still predict the data? Are there less data-intensive methods that could still provide accurate predictions?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|29|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "Why does random-forest performs poorly in the regression task with the Lotka-Volterra simulations but it is the best-performing algorithm in real communities? Any hypotheses?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|29|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "L100- I wonder if there is a way to map these variables in figure 1 for extra clarity.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|29|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "L170 - State in the Lotka-Volterra results that random forest performs poorly at all sizes.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|29|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "L230. Why are regression results not presented for E. faecium? in the main text and figure 3?", "reviewer_type": "human", "label": "error", "error_type": "Neglect", "label_origin": "expert+llm-filter"}
{"id": "prb|29|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "Figure 1. Make invading species clearer, maybe the lines of other species in the community should be shades of gray.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|29|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "Figure 2B. Is this real data? Which communities are these?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|29|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "Throughout the work, the authors use Receiver Operator Characteristic (ROC) curves to evaluate the accuracy of their colonization classifiers, and conclude that classification is accurate when the area under the curve ROC curve (AUROC) is greater than 0.8 (line 155).\\n\\nWhile the use of these methods is standard in machine learning, I worry that using unqualified terms like “accurately predict” / “successfully predict” / “predictable” as a stand in for this technical definition might be confusing for microbial ecologists, who might be more inclined to interpret them according to their standard English usage.\\n\\nWhat the manuscript strongly shows is that the trained classifiers are better than random guessing (AUROC=0.5), but there is a large gap between that and “successful prediction”. I think the manuscript would be improved if the authors could revise their language throughout the work to make their accuracy limitations more clear. E.g., a plain reading of the current version of the abstract might give the impression that there are no accuracy limitations at all. The use of “predictable” in the section heading on line 196 is similarly confusing, as is the use of “can solve the classification problem” on line 233 . The results are already impressive, so some extra clarity on this front would be helpful for avoiding confusion within the field.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|29|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "In addition to clarifying the language, it would be helpful to provide some guidance for how ROC curves and AUROC scores translate to accuracy in real experiments. E.g. what is the best total accuracy (true positives + true negatives / total) that can be achieved for a given classifier, regardless of its internal threshold? (this would work well for balanced examples like the one here, but would need to be tweaked for less permissive colonization)", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|29|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "Likewise, to get some intuition for the AUC scores / accuracy scores, it could be useful to compare the machine learning methods to an even simpler classifier based on total community diversity. Given the results of Figs 3B and 4B, this naïve classifier might do pretty well...", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|29|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "For the quantitative prediction task (predicting the relative abundance at steady state), the authors use the Pearson correlation as a measure of accuracy. I was confused the correlation metric was used, rather than raw sum of squared differences between the observed and predicted values. (The latter would seem to more closely match what one would be looking for in an experiment.)\\n\\nAlso, I couldn’t tell from the methods whether the R^2 values were calculated from the relative abundances or their log transformed values; Fig 4H-J suggests the latter but would be good to clarify.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|29|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "The relative abundance prediction results did not appear to be shown for E. faecalis (but I assume that they were constructed in order to calculate the CI scores in Fig. 5). Regardless, I think it would be good to show the results of this prediction task for both species; if the results are not as good as they were for A. muciniphila, it would be good for readers to know that this prediction method is less accurate for some species.", "reviewer_type": "human", "label": "error", "error_type": "Neglect", "label_origin": "expert+llm-filter"}
{"id": "prb|29|Human_3|7", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "I couldn’t quite tell from the methods how the antibiotic-treated communities were derived. Was it a single pulse of antibiotics? Or continuous addition to the media (including during the invasion event)?", "reviewer_type": "human", "label": "error", "error_type": "Neglect", "label_origin": "expert+llm-filter"}
{"id": "prb|29|Human_3|8", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "I couldn’t tell from the methods how the perturbations used to define “colonization impact” (CI) scores were chosen. What were the magnitudes and/or signs of the perturbations?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|29|Human_3|9", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "It is known that GLV models exhibit limit cycles and chaotic dynamics, so that they do not always have a steady state. How would you apply the method in that case? Were the parameters chosen in a special way to avoid this behavior?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|29|Human_3|10", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "I couldn’t tell how the self-interaction terms were chosen in the GLV model. Please clarify.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|29|Human_3|11", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "The GLV model works with absolute abundances, while the data are compositional (relative abundance). Could this influence the differences between the colonization interactions in Fig. 5B? Ideally, the authors could convert their GLV abundances into relative abundances to make their simulations more like their data. Is the analytical result in Eq. 4 still valid in the compositional domain?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|29|Human_3|12", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "Similar results to Eq. 4 have been utilized in cavity method approaches to GLV models (e.g. Bunin Phys Rev E 2017). These should be cited around line 158-160, along with the new derivation.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|29|Human_3|13", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "If I understand correctly, the result in follows almost immediately from the definition of the GLV model (similar to Eq. 2), if we make the additional assumption that A is invertible. This seems like a pretty strong assumption, so it might be best to say that *some* GLV models satisfy this derivation. Are the parameter chosen in a special way here to ensure that A is invertible?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|29|Human_3|14", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "The use of \\\"established\\\" on line 174 does not seem appropriate, given that similar experiments were performed in the cited reference. I’d suggest changing this to something like “used” instead.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|29|Human_3|15", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "The use of the term “the data driven approach” is confusing, since there are many possible ways to use data to inform prediction. I’d suggesting changing this to “data driven approaches” or “our data-driven approach”, depending on the context, so that readers will know what is being referred to.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|29|Human_3|16", "source": "prb", "split": "test", "paper_id": "prb29", "comment": "Related to the previous point, several earlier studies have used data-driven approaches to predict competition and colonization gut microbiome-like communities (e.g. Buffie et al Nature 2015, Venturelli et al Mol Sys Biol 2018). They used slightly more parameterized models (e.g. GLV in this case) but are still conceptually related to the approaches present work. These contributions should be cited somewhere in the introduction (e.g. around line 80).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|31|Claude|1", "source": "prb", "split": "test", "paper_id": "prb31", "comment": "The paper draws conclusions about GECKO-generated ecModels outperforming ME-models based on a comparison that does not account for fundamental differences in model architecture, objectives, and simulation methodologies between the two frameworks. This comparison conflates model performance with methodological differences, leading to potentially misleading conclusions about the relative merits of GECKO.\n\n\"The sum squared error (SSE) for batch growth rate predictions across the 11 carbon sources using eciML1515 was 0.27, a drastic improvement when compared to the 1.21 SSE of iJL1678 ME-model predictions32.\"\nThis comparison presents SSE values without acknowledging that the ME-model (iJL1678b) is substantially more complex than GECKO ecModels, including detailed representations of gene expression, transcription, and translation machinery. ME-models solve a fundamentally different optimization problem and are not designed primarily for growth rate prediction but for understanding proteome allocation and expression constraints. The paper does not discuss whether the same parameterization, solver settings, or optimization objectives were used for both models, making the SSE comparison potentially misleading.\n\"Figure 3B shows the predicted total proteome needed by cells to sustain the provided experimental growth rates for the same 11 environments. Notably eciML1515 predicts values that lie within the range of predictions of the iJL1678 ME-model (from the optimal to the generalist case) for 10 out of the 11 carbon sources\"\nThe ME-model provides a range of predictions (optimal to generalist) because it models proteome allocation strategies explicitly. GECKO ecModels provide a single prediction that falls within this range, which does not demonstrate superiority but rather shows that GECKO predictions are consistent with one of many possible proteome allocation strategies that ME-models can represent. This framing inappropriately positions GECKO as \"better\" when it simply provides less nuanced predictions.\n\"Using the iJL1678b ME-model of E. coli K-12 MG1655 [...] which inherently provides predictions of the functional proteome required to sustain a particular metabolic phenotype, including cofactor usage.\" [[1]](#citation-list)\nAccording to published literature on ME-models, these models are designed to capture proteome allocation and gene expression constraints, which is a fundamentally different objective than simple growth rate prediction. The comparison in this paper does not account for these architectural and purpose-driven differences, leading to an apples-to-oranges comparison that could mislead readers about the relative utility of each approach.\n\nReferences:\n[1] Patel, A., Mao, L., Long, F., et al. (2020). Computation of condition-dependent proteome allocation reveals variability in the macro and micro nutrient requirements for growth. *PLOS Computational Biology*, 16(4), e1007817. https://journals.plos.org/ploscompbiol/article?id=10.1371/journal.pcbi.1007817", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|31|Claude|2", "source": "prb", "split": "test", "paper_id": "prb31", "comment": "The validation of the improved kcat matching algorithm is based on Kolmogorov-Smirnov tests comparing the distribution of matched kcats to BRENDA reference distributions, rather than validating whether individual kcat assignments are accurate for specific reactions. This distributional validation does not demonstrate that the assigned parameters are biologically meaningful for the reactions to which they are assigned.\n\n\"Moreover, the implementation of the phylogenetic distance-based criterion yielded a distribution of kinetic parameters that showed no significant differences when compared to the values reported in BRENDA for all fungi species, in contrast to the kinetic profile matched by the previous algorithm (p-values <10^{-10} and <10^{-7}, when compared to the BRENDA fungi and S. cerevisiae distributions, respectively, under a Kolmogorov-Smirnov test)\"\nThe Kolmogorov-Smirnov test assesses whether two samples come from the same distribution, but matching the overall distribution of kcats does not ensure that individual reactions receive appropriate kcat values. A randomly assigned set of kcats drawn from the BRENDA fungi distribution would pass the same statistical test but would not produce a biologically meaningful model. The validation conflates distributional accuracy with reaction-specific accuracy.\n\"The quality of phenotype predictions for the ecYeast7 model enhanced by GECKO2.0 was evaluated by simulation of batch growth in 19 different environments, with an average relative error of 23.97% when compared to experimental data, in contrast, its GECKO1.0 counterpart yielded an average relative error of 32.07%.\"\nWhile the improvement in growth rate predictions is presented, no confidence intervals, standard deviations, or statistical tests are provided to assess whether this 8% improvement is statistically significant. Additionally, growth rate predictions depend on many factors beyond kcat accuracy, including model topology, biomass composition, and constraint settings. Better growth rate predictions do not necessarily validate that individual kcat assignments are correct.\n\"Because not all enzymes can be mapped to a reaction uniquely and proteomics data still suffer from incomplete coverage, kapp,max has a low coverage of the metabolic network and cannot be readily used in genome-scale models.\" [[2]](#citation-list)\nPublished work on in vivo kcat estimation highlights that the discrepancy between in vitro kcat values (like those in BRENDA) and apparent in vivo catalytic rates can be substantial. The GECKO method's reliance on BRENDA parameters, even with phylogenetic corrections, may not capture these in vivo effects. The literature shows that in vivo kcat estimates can be significantly different from in vitro values, yet this validation gap is not addressed in the paper.\n\nReferences:\n[2] Heckmann, D., Zielinski, D.C., Patel, A., et al. (2020). Kinetic profiling of metabolic specialists demonstrates stability and consistency of in vivo enzyme turnover numbers. *Proceedings of the National Academy of Sciences*, 117(37), 23182-23190. https://www.pnas.org/doi/10.1073/pnas.2001562117", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|31|Claude|3", "source": "prb", "split": "test", "paper_id": "prb31", "comment": "The paper claims that proteomics-constrained ecModels improve phenotype predictions, but Figure 4 shows that this improvement is inconsistent across organisms and conditions. In several cases, proteomics constraints do not improve predictions over simpler ecModel or GEM approaches, undermining the claimed universal benefit of proteomics integration.\n\n\"It was found that the addition of the enzyme pool constraint enables major reduction of the relative error in prediction of gaseous exchange fluxes in some of the studied conditions. Additionally, the incorporation of individual protein abundance constraints\"\nThe phrase \"in some of the studied conditions\" acknowledges that the improvement is not consistent. For a method to be validated as generally beneficial, improvements should be demonstrated across the majority of conditions. The paper does not quantify what proportion of conditions show improvement or provide statistical tests to assess the significance of observed differences.\n\"Comparison of median relative error in prediction of exchange fluxes for O2 and CO2 by GEMs, ecModels and proteomics-constrained ecModels across diverse conditions (chemostat cultures at 0.1 h-1 dilution rate) for A) S. cerevisiae B) K. marxianus C) Y. lipolytica.\"\nThe validation relies solely on prediction of gaseous exchange fluxes (O2 and CO2), which is a narrow validation basis. Comprehensive validation of proteomics-constrained models should include comparison of predicted enzyme usages with measured protein abundances, flux predictions for multiple metabolites, and growth phenotypes. Using only two exchange fluxes limits the conclusions that can be drawn about model accuracy.\n\"It was found that incorporation of proteomics constraints does not affect enzyme demand predictions significantly for most of the active enzymes at low dilution rates across the simulated conditions.\"\nThis statement from the Results/Discussion section appears to contradict the claimed benefits of proteomics integration. If proteomics constraints do not significantly affect enzyme demand predictions for most enzymes, the added complexity of incorporating proteomics data may not provide commensurate benefits for model accuracy. This limitation is buried in the text rather than prominently addressed as a key finding.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|31|GPT|1", "source": "prb", "split": "test", "paper_id": "prb31", "comment": "This paper’s automatic kinetic-parameter “curation” procedure undermines validity because it forces ecModels to match experimental growth by replacing limiting turnover numbers with extreme (maximal) values, which can yield overfitted and non-biological kinetics and thereby compromise the reported predictive accuracy and any downstream mechanistic interpretations that depend on those constraints.\n\n\"For automatically generated ecModels that are not able to reach the provided experimental value for maximum batch growth rate, an automatic module performs a series of steps in which the top enzymatic limitation on growth rate is identified through the quantification of enzyme control coefficients. For such enzymes, the E.C. number is obtained and then its correspondent \\( k_{cat} \\) value is substituted by the highest one available in BRENDA for the given enzyme class. This procedure iterates until the specific growth rate predicted by the model reaches the provided experimental value.\"\nThis describes a calibration loop that explicitly targets the maximum growth rate by increasing the most limiting kinetic parameters, rather than validating kinetics independently. Choosing “the highest one available” is a worst-case optimistic assumption because BRENDA aggregates heterogeneous assays across conditions, isoforms, and organisms, so the maximum is rarely representative of the modeled in vivo context. Iterating until the model matches the experimental growth rate can create many alternative parameter sets that satisfy the same target, so it does not establish identifiability or mechanistic correctness of the fitted kcat values. Because enzyme constraints are central to ecModel feasibility and predicted enzyme usage, this procedure can strongly shape later conclusions (e.g., which pathways appear “protein-limited” or “highly saturated”). Without sensitivity analyses showing that the biological conclusions remain stable under less aggressive (and more realistic) parameter adjustments, the core claims about predictive quality and inferred enzyme limitations remain weak.\n```matlab\n%Gets the maximum Kcat value for the queried EC#\nif ~isempty(matching)\n    [Kcat, maxIndx] = max(BRENDA{4}(matching));\n    orgK            = BRENDA{3}(matching(maxIndx));\nend        \n...\n%Gets the maximum SA*Mw value for the queried EC#\nif ~isempty(matching)\n    [SA_Mw, maxIndx] = max(SA_cell{3}(matching));\n    SA_Mw            = SA_Mw; %[1/hr]\n    orgS             = SA_cell{2}(matching(maxIndx));\nend        \n%Choose the maximal available value as a turnover number for the EC\nvalue  = [value; max(Kcat,SA_Mw)];\n```\nThis implementation explicitly operationalizes the “choose the highest” strategy by selecting the maximum available turnover-like value (either kcat or SA·MW-derived) from the database matches. Using the maximum across all matched entries further amplifies the optimistic bias introduced by relaxed matching (e.g., when wildcards broaden EC matches), since broader pools increase the chance of extreme outliers. The comment “Choose the maximal available value as a turnover number” indicates that maximality is a design goal rather than an accidental artifact, reinforcing that this behavior is systematic. Such maximal selection is known to be problematic when kcat values are inconsistent across literature sources and assay conditions, because maxima are particularly sensitive to those inconsistencies. As a result, the growth-matching and “high coverage” narratives risk being achieved by parameter inflation rather than improved biological realism.\n\"Finally, the mean value of all collected kcat values is chosen. For all reactions for which no kcat value could be found, a default kcat representing the median of all found kcat values is set.\" [[3]](#ref3)\nThis describes a contrasting, more conservative practice in automated enzyme-constraint pipelines: aggregating multiple candidate kcat values and using a central tendency (mean/median) rather than a maximum. While mean/median choices are not perfect, they reduce sensitivity to outliers and better reflect typical kinetic capabilities under varied measurement conditions. The fact that AutoPACMEN still emphasizes subsequent calibration/validation steps underscores that enzyme-constrained models need careful fitting and checking, but not necessarily by maximizing individual kcat entries. Compared to this, the reviewed paper’s “replace with the highest available” approach is more likely to systematically overestimate catalytic capacity and distort protein-limitation patterns. This difference matters because the paper’s central contributions involve automating parameterization for many organisms; an aggressive maximality heuristic can propagate biased kinetics at scale.\n\nReferences:\n[3] [Bekiaris, P. S., & Klamt, S. (2020). Automatic construction of metabolic models with enzyme constraints. *BMC Bioinformatics*, 21:19.](https://pmc.ncbi.nlm.nih.gov/articles/PMC6961255/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|31|GPT|2", "source": "prb", "split": "test", "paper_id": "prb31", "comment": "This paper’s proteomics-constrained ecModel workflow is not sufficiently valid for drawing mechanistic conclusions (e.g., “high saturation” and “metabolic robustness”) because it explicitly discards or relaxes proteomics constraints to enforce model feasibility and introduces strong, under-validated optimization assumptions, without reporting how often and how much these steps alter the data-driven constraints.\n\n\"In order to allow for GECKO simulations, we added a new feature to the platform for uploading enzyme-constrained models and absolute proteomics data. Additionally, we added a simulation algorithm that recognizes said models, and overlays the selected proteomics data on them, leaving out data that makes the model unable to grow at a pre-specified growth rate.\" \nThis text explicitly states that proteomics measurements can be excluded when they conflict with a growth-feasible model, meaning the “proteomics-constrained” model may not actually be constrained by the full measured proteome. Because enzyme saturation is computed as predicted usage divided by measured abundance, removing abundance constraints for problematic proteins can directly change which enzymes appear highly saturated and which pathways appear limiting. The procedure also risks a selection bias: constraints are kept preferentially when they are consistent with the modeling assumptions (e.g., feasible growth at a target rate), which can artificially strengthen apparent agreement. The paper does not quantify how much data is “left out,” which is essential for assessing whether results reflect biology or constraint-filtering. Without reporting per-condition constraint retention/relaxation rates and performing sensitivity analyses to these choices, the robustness/saturation conclusions are not well supported.\n```matlab\n%   Flexibilize enzyme concentration of an ecModel with constrained with\n%   proteomics data. The upper bound of the protein usage reaction is\n%   changed, while the concentrations in ecModel.ec.concs remain unchanged.\n...\n% Output:\n%   model           ecModel where the constraint of measured enzyme\n%                   concentrations have been flexibilized (=relaxed) in the\n%                   S-matrix, to allow the model to reach the growth rate\n%                   defined in expGrowth, while the values in\n%                   ecModel.ec.concs have remained untouched.\n```\nThis code documents a deliberate mechanism to relax (“flexibilize”) enzyme-usage bounds while keeping the original measured concentrations unchanged, explicitly to reach a target growth rate. That design creates a mismatch between what is reported as “measured” abundance and what is actually enforced as a constraint during simulation, which can invalidate quantitative interpretations of enzyme saturation. Because saturation analyses in the paper hinge on ratios of predicted usage to abundance, relaxing usage bounds can reassign limitation away from measured enzymes and toward the “unmeasured protein pool,” changing the inferred adaptation mechanisms. The code also frames overconstraint as expected (“may occur”), implying that relaxation is a routine rather than exceptional step, further elevating its impact on results. The paper does not provide the key audit trail typically expected in proteomics-constrained modeling: which proteins were relaxed, by what factor, and how those interventions affect reported pathway-level burdens and saturation sets.\n\"Absolute proteomic quantification techniques are still suffering from high variation\" [[4]](#ref4)\nThis external statement supports the authors’ premise that absolute proteomics can be noisy, but it simultaneously raises the bar for transparency when proteomics is used as a hard constraint. High variation means that constraint relaxation strategies can easily become dominant determinants of model outputs unless they are carefully documented and stress-tested. In best practice, one would report replicate-level variability, missingness, and the exact rules used to reconcile data with model feasibility, plus show that biological conclusions are stable across reasonable alternatives. The reviewed paper acknowledges variability but does not provide enough quantitative reporting on relaxation/exclusion steps to judge whether conclusions are robust. Consequently, key mechanistic claims (e.g., conserved “high saturation” enzymes and “metabolic robustness”) remain insufficiently supported.\n\nReferences:\n[4] [Heckmann, D. et al. (2020). Kinetic profiling of metabolic specialists demonstrates stability and consistency of in vivo enzyme turnover numbers. *PNAS*, 117(37), 23182–23190.](https://www.pnas.org/doi/10.1073/pnas.2001562117)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|31|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb31", "comment": "The paper employs a \"fuzzy matching\" algorithm that assigns $k_{cat}$ values from any organism or any substrate (levels 4-6) when specific data is missing, which introduces significant and unquantified uncertainty into the models.\n\n`fuzzyKcatMatching.m`\n```matlab\n%                           4: any organism, any substrate, kcat\n%                           5: correct organism, specific activity\n%                           6: any organism, specific activity\n```\nThe code explicitly allows the assignment of $k_{cat}$ values from \"any organism\" and \"any substrate\" (level 4) or from specific activities of \"any organism\" (level 6). Given that $k_{cat}$ values can vary by orders of magnitude between organisms and substrates [1], using a value from a phylogenetically distant organism for a different substrate is scientifically unsound and likely results in highly inaccurate constraints.\n\"Figure 1 ... D) Number of kcat matches in ecYeast7 per assignment category (GECKO 2.0).\"\nWhile the paper reports the *number* of matches per category, it does not provide an error analysis or validation of the accuracy of these \"fuzzy\" matches against experimental ground truth (e.g., via leave-one-out cross-validation). The reliance on such loose matching criteria for a significant portion of the network undermines the claim of generating \"high-quality\" models.\n\nReferences:\n[1] Kroll, A. et al. Advances in Machine Learning Models for Predicting Enzyme Kinetic Parameters. J. Chem. Inf. Model. 61, 2758–2768 (2021). https://pubs.acs.org/doi/10.1021/acs.jcim.1c00642", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|31|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb31", "comment": "The \"flexibilization\" procedure used to integrate proteomics data iteratively relaxes constraints until the model matches the experimental growth rate, which effectively masks errors in $k_{cat}$ values or proteomics data and reduces the model's predictive capability.\n\n`flexibilizeEnzConcs.m`\n```matlab\n%   Flexibilize enzyme concentration of an ecModel with constrained with\n%   proteomics data. The upper bound of the protein usage reaction is\n%   changed...\n%   while predGrowth < expGrowth\n%       ...\n%       % replace the UB\n%       model.lb(protUsageIdx) = -(model.ec.concs(protConcs(maxIdx)) * (1+increase));\n```\nThe code demonstrates that if the model cannot reach the experimental growth rate, the algorithm arbitrarily increases the upper bound of the limiting enzyme's usage. This creates a circularity: the model is forced to fit the phenotype by overriding the input data (proteomics constraints). If a $k_{cat}$ value is underestimated (a common issue), this procedure will artificially inflate the enzyme concentration to compensate, hiding the parameter error rather than identifying it.\n\"some of the incorporated data constraints need to be loosened in order to obtain functional ecModels.\"\nThe authors acknowledge this \"loosening\" but do not quantify how much the final \"flexibilized\" constraints deviate from the measured proteomics data. This fitting process compromises the validity of the model as a tool for *predicting* phenotypes from omics data, as the data is modified to fit the phenotype.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|31|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb31", "comment": "The comparison between the GECKO-generated model (`eciML1515`) and the ME-model (`ME-iJL1678`) is superficial and misleading, as it compares a simplified, fitted model against a mechanistic *ab initio* model on metrics where the former has an inherent advantage due to parameter fitting.\n\n\"The sum squared error (SSE) for batch growth rate predictions across the 11 carbon sources using eciML1515 was 0.27, a drastic improvement when compared to the 1.21 SSE of iJL1678 ME-model predictions\"\nThis comparison ignores the fundamental difference in scope between the two modeling frameworks. ME-models [2] predict the entire gene expression machinery and resource allocation *ab initio*, which is a much harder problem than the GECKO approach of using a fixed protein pool or input proteomics data. Comparing them solely on growth rate prediction accuracy, especially when GECKO models are often tuned (flexibilized) to match growth phenotypes, creates a false equivalence and fails to acknowledge the superior biological insight (e.g., translation efficiency, codon usage) provided by ME-models.\n\"Figure 3 ... B) Prediction of total protein content in the cell by eciML1515 and ME-iJL1678 using the optimal and generalist approaches.\"\nThe GECKO model's protein content prediction is largely a function of the metabolic flux and the assigned $k_{cat}$ values, whereas the ME-model predicts the synthesis of the protein machinery itself. Presenting them side-by-side without explicitly discussing this difference in model complexity and input requirements is misleading to readers who may not be familiar with the intricacies of ME-models.\n\nReferences:\n[2] Lloyd, C. J. et al. COBRA ME: A computational framework for genome-scale mechanistic models of metabolism and gene expression. BMC Syst. Biol. 12, 93 (2018). https://bmcsystbiol.biomedcentral.com/articles/10.1186/s12918-018-0609-9", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|31|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb31", "comment": "The claim that the upgraded GECKO toolbox allows for the reconstruction of enzyme-constrained models for \"any organism\" is not sufficiently supported by the validation, which is limited to well-studied model organisms.\n\n\"Here, we upgraded the GECKO toolbox in order to enhance models with enzyme and proteomics constraints for any organism with an available GEM reconstruction.\"\nThe validation in the paper is restricted to *S. cerevisiae*, *K. marxianus*, *Y. lipolytica*, *E. coli*, and *H. sapiens*. All these organisms have relatively rich data in BRENDA. For less-studied organisms, the \"fuzzy matching\" algorithm would rely heavily on the \"any organism\" or \"any substrate\" categories (levels 4-6), which, as noted in Item 1, are highly unreliable. The paper does not demonstrate the performance of the toolbox on a non-model organism where data scarcity would be a major bottleneck, thus the claim of \"any organism\" applicability is overgeneralized.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|31|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb31", "comment": "Authors mention in Lines 151-152 that the results derived from GECKO “are highly sensitive to the distribution of incorporated kinetic parameters”. However, they do not sufficiently describe how they address this issue. We can find the same enzyme with very different kcats under different experimental contexts. How general are the values provided in BRENDA for the simulated conditions? In fact, authors show in Supplementary Note 1 the dispersion found in different enzymes. However, they do not explain which kcat value must be taken. For example, the median value, maximum value?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|31|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb31", "comment": "“A modified set of hierarchical kcat matching criteria was implemented as part of GECKO 2.0” (Lines 175-176). This is possibly the most important change with respect to the previous version. It should be described in Methods section and not in Supplementary Note 2. For this reason, Figure 1D is difficult to follow in the main text. How did authors validate the use of a phylogenetic distance to infer kcats?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|31|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb31", "comment": "Authors report an improvement in predicting batch growth in 19 environments with respect their previous algorithm: 23.97% vs 32.07 relative error? Is that difference significative? How was this error calculated? Did authors calibrate the model using sensitivity analysis? This is something tricky and overfitting could be a problem in the derived model? Did authors test their new model with experimental that were not used to calibrate the model? This is important and not described in the text.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|31|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb31", "comment": "Figure 3: Authors report an improvement in growth rate prediction capacity of E. coli in comparison with ME-model. Could authors show correlation instead of sum of square errors (SSE)?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|31|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb31", "comment": "Figure 4: “Additionally, the incorporation of individual protein abundance constraints improves even further the predictive accuracy of gaseous exchanges, for 10 out of the 11 evaluated cases”. I am missing something. I can see 4 points out of 11 where no improvement is obtained: std in yeast, std y osm in K. marxianus and HiT in Y. lipolytica. Is this result statistically significant? Has this experimental design enough power? Given the number of parameters required in ec-Models, in comparison with GEMs, could it be this only overfitting?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|31|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb31", "comment": "What do authors mean by “wild-cards”? (Line 189)", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|31|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb31", "comment": "The authors mention that additional condition-dependent exchange fluxes of byproducts can be used as constraints in order to limit the feasible solution space. How does the user decide which condition-specific exchange fluxes need to be used in a particular condition? Can the authors support this with an example?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|31|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb31", "comment": "Can the authors define what are \\\"active fluxes\\\" in the context of metabolic fluxes?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|31|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb31", "comment": "How does the method handle reactions that are not associated with enzymatic activities? For example, some exchange and transport reactions that do not have any GPRs associated.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|31|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb31", "comment": "Based on the Kcat distribution in BRENDA, is it possible to predict the minimum cut-off needed for constraining the GEM of other organisms like Mtb, Mus musculus, Arabidopsis etc.?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|31|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb31", "comment": "In case of multi-omics data available for organisms like yeast and humans, is it possible to integrate that information in the model along with the proteins to constrain the model and obtain biologically meaningful predictions?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|31|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb31", "comment": "How much is the computing time needed for analyzing the ecModels considering the fact that they are of different sizes (reactions, metabolites and proteins)?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|31|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb31", "comment": "The term \\\"eukaryal\\\" is not commonly used term. It is more appropriate to use the term \\\"eukaryote\\\" for S. cerevisiae.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|31|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb31", "comment": "In line 363-364 the authors mentioned \\\"This suggests that upper bounds on enzyme usages induce differentiated utilization of isoenzymes, reflecting well why isoenzymes have been maintained throughout evolution\\\". Can the authors elaborate more on some examples of isozymes to support their point?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|31|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb31", "comment": "Did the authors use fastFVA for the analysis shown in this paper?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|32|Claude|1", "source": "prb", "split": "test", "paper_id": "prb32", "comment": "The parity plots in Figure 5 show predictions from the single best-performing fold (selected based on minimum test MAE), while the error statistics reported in the legends are averaged across all 10 folds of cross-validation. This creates a visual impression of model performance that is better than what the averaged statistics suggest.\n\n\"The parity plots comparing GPR predictions with experimental measurements of 28 additives and the baseline systems are shown in Fig. 5. Based on the results, the highest prediction accuracy is observed for final specific capacity model (Test MAE^10−fold CV = 10.7 ± 4.6 mAhg⁻¹)\"\nThe paper reports averaged MAE statistics from 10-fold cross-validation, which is appropriate. However, examination of the provided code reveals that the actual data points shown in the parity plots are not representative of this average performance but rather come from the best-performing fold, creating an inconsistency between the visual representation and the reported statistics.\n\n* Quote (from MLmodels.ipynb):\n```python\nif mae_test < best_score:\n    best_score = mae_test\n    best_model = model\n    X_train_best[prop] = X_train\n    X_test_best[prop] = X_test\n    y_train_best[prop] = y_train\n    y_test_best[prop] = y_test\n```\nThis code shows that the model and data splits are selected based on the minimum test MAE across all folds. This \"best\" fold is then used for visualization, which systematically presents an optimistic view of model performance since the selection criterion inherently favors the fold where the model happened to perform best.\n\n* Quote (from MLmodels.ipynb):\n```python\nplt.errorbar(y_train_best[prop], y_pred_train, yerr= std_train, fmt='o', capsize=8, c=train_cl, alpha=1., \n            ms=markerSize, lw=2.5, label=r\"$\\rm Train, MAE^{10-fold \\ CV}$ = \"+str(round(average_mae_train[prop],1))+\" ± \"+str(round(std_mae_train[prop],1)))\nplt.errorbar(y_test_best[prop], y_pred_test, yerr= std_test, fmt='s', capsize=8, c=test_cl, alpha=1., \n            ms=markerSize, lw=2.5, label=r\"$\\rm Test, MAE^{10-fold \\ CV}$ = \"+str(round(average_mae_test[prop],1))+\" ± \"+str(round(std_mae_test[prop],1)))\n```\nThe plotting code explicitly uses the best fold's data (y_train_best, y_test_best) for visualization while labeling with averaged statistics (average_mae_train, average_mae_test). Standard machine learning practice would be to either show all folds' data points, show predictions from a model trained on all data, or clearly indicate that the visualization represents only the best-performing fold. This methodological inconsistency can mislead readers about the true predictive capability of the models.\n\"Cross-validation is a model evaluation technique used to assess how well a machine learning model generalizes to unseen data... By evaluating models across multiple data splits, cross-validation provides a realistic view of performance\" from [What Is Cross-Validation in Machine Learning][1]\nThe purpose of k-fold cross-validation is to provide a robust estimate of model performance by averaging across multiple data splits. Selectively displaying results from only the best-performing fold contradicts this principle and undermines the reliability of the visual assessment. Readers viewing Figure 5 would reasonably assume the displayed points are representative of average model performance, not the cherry-picked best case.\n\nReferences:\n[1] [What Is Cross-Validation in Machine Learning - LinkedIn](https://www.linkedin.com/pulse/what-cross-validation-machine-learning-durgesh-kekare-kgvnc)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|32|Claude|2", "source": "prb", "split": "test", "paper_id": "prb32", "comment": "Table 1 appears to contain replicate measurements for the same additive compositions (e.g., entries for \"LiDFOB 1.0 wt% + SA 1.0 wt%\" and \"LiDFOB 1.0 wt% + MS 1.0 wt%\" appear multiple times with different values), but the paper does not present averaged results with error bars or perform any statistical analysis to establish significance of performance differences despite the large variability observed.\n\n* Quote from Table 1: \"No. 29 | LiDFOB 1.0 wt% + SA 1.0 wt% | 41.19 | 16.26 | 91.79\" and \"No. 31 | LiDFOB 1.0 wt% + SA 1.0 wt% | 50.13 | 16.77 | 92.17\"\nThese two entries show the same additive composition but with different ASI values (41.19 vs 50.13 Ω·cm²), suggesting these may be replicate experiments. If so, the ~22% difference in ASI between replicates represents substantial cell-to-cell variability that should be quantified with proper error analysis. The paper does not acknowledge this variability or present averaged values with standard deviations.\n\n* Quote from Table 1: \"No. 30 | LiDFOB 1.0 wt% + MS 1.0 wt% | 104.76 | 65.57 | 69.80\" and \"No. 33 | LiDFOB 1.0 wt% + MS 1.0 wt% | 203.43 | 110.36 | 80.06\"\nThese apparent replicates show nearly 2× difference in ASI (104.76 vs 203.43 Ω·cm²) and approximately 70% difference in ∆ASI (65.57 vs 110.36 Ω·cm²). Such extreme variability raises serious questions about whether the electrochemical measurements are reproducible and whether any conclusions about additive performance can be considered robust without proper statistical treatment.\n\"More importantly, the addition of either MS or SA to LiBOB show notable enhancement in all three considered metrics, with the combination of LiBOB at 1.0 wt% and SA at 1.0 wt% achieving the highest final specific capacity (95.49 mAhg⁻¹) among all additives in this work.\"\nThis conclusion about \"notable enhancement\" is drawn without statistical analysis. The difference between 95.49 mAhg⁻¹ (LiBOB+SA) and 91.94 mAhg⁻¹ (baseline) is only ~3.9%, which is comparable to or smaller than the variability observed between apparent replicates in Table 1. Without proper error analysis, claims of \"enhancement\" cannot be statistically justified.", "reviewer_type": "ai", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|32|Claude|3", "source": "prb", "split": "test", "paper_id": "prb32", "comment": "The StandardScaler used to transform the 125 unknown additive combinations for prediction was fitted only on the training subset of the last cross-validation fold, not on the complete dataset, creating an inconsistency in the preprocessing pipeline that affects reproducibility.\n\n* Quote (from MLmodels.ipynb):\n```python\n# Inside the k-fold loop (line 126-127)\nsc = StandardScaler()\nX_train = sc.fit_transform(X_train)\n```\nThe StandardScaler object `sc` is created and fitted inside the k-fold cross-validation loop. Since the loop iterates through all 10 folds, the scaler at the end of the loop contains statistics (mean and standard deviation) from only the last fold's training subset, not from the complete dataset of 29 samples.\n\n* Quote (from MLmodels.ipynb):\n```python\n# Outside all loops (line 330)\nX_newAdd = sc.transform(dfEnumFeats)\n```\nThe unknown features are transformed using the scaler from the last cross-validation fold. This means approximately 26 training samples determined the scaling parameters, rather than all 29 samples. While the impact may be minor in this case, this practice violates the principle of using consistent preprocessing for training and prediction.\n\"To ensure model generalization and avoid data leakage, normalization parameters were calculated exclusively from the training set and then applied to the test data\" from [Machine learning-based prediction of well performance][2]\nStandard machine learning practice dictates that for making predictions on new data, the scaler should be fitted on all available training data (in this case, all 29 samples), not on a subset from one cross-validation fold. This methodological error affects the reproducibility of results since different random seeds would produce different final scalers.\n\nReferences:\n[2] [Machine learning-based prediction of well performance - Nature Scientific Reports](https://www.nature.com/articles/s41598-025-27851-8)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|32|GPT|1", "source": "prb", "split": "test", "paper_id": "prb32", "comment": "The manuscript’s central “prediction and validation” step (ranking 125 untested additive pairs and selecting the top 6) is not methodologically sound because the provided notebook applies an inconsistent (and non-reproducible) feature standardization when predicting the 125 candidates and additionally mislabels predictive variance as a standard deviation, directly undermining the validity and reliability of the reported ML-guided recommendations.\n\n\"Using our trained GPR models, we performed prediction of ASI, ∆ASI, and Q for 125 unknown additive candidates.\" \nThis sentence is a key methodological claim: the paper’s main contribution depends on correctly generating predictions for the 125 “unknown” additive combinations. If prediction preprocessing differs from training preprocessing, the model is effectively evaluated out-of-distribution in feature space even when the raw inputs are in-distribution. This is especially consequential when candidates are ranked (rather than merely predicted) because small systematic shifts can change the ordering and therefore which additives are experimentally validated. Because the paper uses these predictions to choose the “top 6” for validation, any systematic preprocessing mismatch directly threatens the paper’s primary conclusion that ML identified superior additives. The issue is not a minor implementation detail; it changes the actual decision rule used for candidate selection. The code provided with the paper must therefore apply the exact same scaling used during model training when generating candidate predictions.\n```python\n# Perform k-fold cross validation\nk_fold = 10\n\n# Split the data into k equal parts\nkf = KFold(n_splits=k_fold, shuffle=True, random_state=42)\nmae_train_list = []\nmae_test_list = []  \nrmse_train_list = []\nrmse_test_list = []\n\nbest_score = float('inf')\nbest_model = None\n\n# Loop over folds\nfor train_index, test_index in kf.split(X):\n    # Split train-test\n    X_train, X_test = X.iloc[train_index], X.iloc[test_index]\n    y_train, y_test = y.iloc[train_index], y.iloc[test_index]\n\n    # Scale the data\n    sc = StandardScaler()\n    X_train = sc.fit_transform(X_train)\n    y_train = np.array(y_train)\n    X_train = torch.tensor(X_train, dtype=torch.float32)\n    y_train = torch.tensor(y_train, dtype=torch.float32)\n\n    X_test = sc.transform(X_test)\n    y_test = np.array(y_test)\n    X_test = torch.tensor(X_test, dtype=torch.float32)\n    y_test = torch.tensor(y_test, dtype=torch.float32)\n```\nThis code (from the provided `MLmodels.ipynb`) shows that a new `StandardScaler()` is fit separately inside each CV fold, meaning there is no single, persistent scaler associated with a final trained model. The notebook does not save `sc.mean_`/`sc.scale_` (or any equivalent) alongside the saved `best_model_*.pth` weights. As a result, reproducing the training-time feature normalization for later inference is impossible from the saved artifacts alone. More importantly, it means that any later call to `sc.transform(...)` for “unknown” candidates will depend on whichever fold’s scaler object happens to remain in scope at the end of execution. This is not a standard or acceptable deployment pattern for ML pipelines where a deterministic preprocessing transform must accompany the model. Since the paper’s main experimental validation depends on these candidate predictions, the absence of a well-defined scaler for inference is a major reproducibility and validity problem.\n```python\n# Make predictions on unknown dataset  \nX_newAdd = sc.transform(dfEnumFeats)\nfor prop in ['FinImpedance', 'DeltaImpedance', 'FinSpcCap']:\n    # Load the saved model and likelihood state dictionaries\n    model_state_dict = torch.load(f'best_model_{prop}.pth')\n    likelihood_state_dict = torch.load(f'best_likelihood_{prop}.pth')\n    likelihood = gpytorch.likelihoods.GaussianLikelihood()\n\n    # Create an instance of the model and likelihood using the loaded state dictionaries\n    model = GPModel(X_train_best[prop], y_train_best[prop], likelihood)\n\n    model.load_state_dict(model_state_dict)\n    likelihood.load_state_dict(likelihood_state_dict)\n\n    # Set the model and likelihood in evaluation mode\n    model.eval()\n    likelihood.eval()\n\n    # Make predictions on new data\n    with torch.no_grad():\n        test_x = torch.tensor(X_newAdd, dtype=torch.float32)  # Sample input data\n        predictions = likelihood(model(test_x))  # Predict the output\n        y_pred_newAdd = predictions.mean  # Get the mean predictions\n        sigma_newAdd = predictions.variance  # Get the predictive variance\n    if prop=='FinImpedance':    \n        resListFinImp = [int(val) for val in y_pred_newAdd.tolist()]\n        resListFinImp_sigma = [int(val) for val in sigma_newAdd.tolist()]\n    elif prop=='IniImpedance':\n        resListIniImp = [int(val) for val in y_pred_newAdd.tolist()]\n        resListIniImp_sigma = [int(val) for val in sigma_newAdd.tolist()]\n    elif prop=='FinSpcCap':\n        resListFinSpcCap = [int(val) for val in y_pred_newAdd.tolist()]\n        resListFinSpcCap_sigma = [int(val) for val in sigma_newAdd.tolist()]\n    elif prop=='DeltaImpedance':\n        resListDeltaImp = [int(val) for val in y_pred_newAdd.tolist()]\n        resListDeltaImp_sigma = [int(val) for val in sigma_newAdd.tolist()]\n```\nThis excerpt shows that the scaler used for candidate prediction is the single variable `sc` from earlier, but `sc` was defined inside the CV loop and is therefore tied to the *last executed fold*, not to a well-defined “final model” for each target property. Consequently, at least two of the three property models will almost certainly receive incorrectly standardized inputs, because nothing in the code binds `sc` to the saved `best_model_{prop}.pth` selected for that property. Additionally, converting both predictions and uncertainties to integers (`int(val)`) discards information and can change ranking decisions when candidates have close scores, which is precisely the regime where multiobjective optimization is sensitive. The code further sets `sigma_newAdd = predictions.variance` but later stores it under “*_std” (see next evidence), conflating variance with standard deviation. Together, these implementation choices mean the published candidate ranking and associated “uncertainty” columns are not trustworthy outputs of the stated probabilistic model.\n```text\nName,SMILES1,SMILES2,FinImpedance,FinImpedance_std,DeltaImpedance,DeltaImpedance_std,FinSpcCap,FinSpcCap_std\nLiDFOB_1+DDD_1,O=C1O[B-](F)(F)OC1=O.[Li+],COC(=O)OCCOC(=O)OC,123,40,51,57,64,29\nLiDFOB_1+BA_1,O=C1O[B-](F)(F)OC1=O.[Li+],CCCC(=O)OC(=O)CCC,94,51,59,54,57,30\nLiDFOB_1+PTSI_1,O=C1O[B-](F)(F)OC1=O.[Li+],Cc1ccc(S(=O)(=O)N=C=O)cc1,80,53,38,62,59,30\n\ndtypes: {'Name': dtype('O'), 'SMILES1': dtype('O'), 'SMILES2': dtype('O'), 'FinImpedance': dtype('int64'), 'FinImpedance_std': dtype('int64'), 'DeltaImpedance': dtype('int64'), 'DeltaImpedance_std': dtype('int64'), 'FinSpcCap': dtype('int64'), 'FinSpcCap_std': dtype('int64')}\n```\nThis excerpt (from the provided `predictedPerformance.xlsx`, rendered as CSV plus inferred dtypes) shows that the published predictions and their “std” values are stored as integers. This is consistent with the notebook’s explicit integer-casting, confirming that ranking decisions could be affected by quantization rather than model differences. It also highlights that the uncertainty columns are labeled as “*_std” even though the notebook computes `predictions.variance`, not a standard deviation. When uncertainty is used as part of the selection criterion (as the manuscript claims), this mislabeling can lead readers to misinterpret the magnitude and units of uncertainty, and can affect downstream decision-making if these spreadsheets are reused. In probabilistic regression, distinguishing variance from standard deviation is essential because they differ by a square root and carry different physical units. The fact that these values are integers further suggests the uncertainty representation is not suitable for calibrated probabilistic decision-making.\n\"Centering and scaling happen independently on each feature by computing the relevant statistics on the samples in the training set. Mean and standard deviation are then stored to be used on later data using transform.\" [[2]](https://scikit-learn.org/stable/modules/generated/sklearn.preprocessing.StandardScaler.html)\nThis documentation describes the standard contract of `StandardScaler`: the training-set statistics are the *state* that must be carried into inference. In the reviewed work, the model is trained on standardized inputs, so inference must apply the same stored means and standard deviations used in training. The notebook does not store or reload these statistics for each trained model, which violates this basic requirement and makes the inference-time preprocessing ambiguous. This is not a pedantic software engineering preference; it is part of the mathematical definition of the model’s input space. For candidate ranking, a mismatch in scaling can systematically shift predictions and invalidate comparisons across candidates. Therefore, the code as provided does not support the manuscript’s claim that the reported candidate predictions are the outputs of the trained models.\n\"@property\\n    def stddev(self) -> Tensor:\\n        # self.variance is guaranteed to be positive, because we do clamping.\\n        return self.variance.sqrt()\" [[3]](https://raw.githubusercontent.com/cornellius-gp/gpytorch/main/gpytorch/distributions/multivariate_normal.py)\nThis GPyTorch source code makes explicit that `stddev` is the square root of `variance`, so treating variance values as standard deviations is a definitional error. In the manuscript, uncertainty is presented as “one standard deviation” (Fig. 5 caption) and also used as part of the argument for reliability in selecting candidates, so a variance/standard-deviation mismatch directly affects the interpretation of uncertainty. Because variance has squared physical units (e.g., (mAh g⁻¹)²), mislabeling it as a standard deviation implies a different unit and magnitude. This can mislead readers about how confident the model is and can distort any uncertainty-aware ranking or filtering. The mismatch is concretely present in the notebook (`predictions.variance`) and the exported spreadsheet columns (`*_std`). Consequently, the paper’s uncertainty-based decision-making is not correctly substantiated by the provided implementation.\n\nReferences:\n[2] [scikit-learn documentation. StandardScaler — scikit-learn.](https://scikit-learn.org/stable/modules/generated/sklearn.preprocessing.StandardScaler.html)\n[3] [GPyTorch source code. `gpytorch/distributions/multivariate_normal.py` (variance and stddev definitions).](https://raw.githubusercontent.com/cornellius-gp/gpytorch/main/gpytorch/distributions/multivariate_normal.py)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|32|GPT|2", "source": "prb", "split": "test", "paper_id": "prb32", "comment": "The manuscript’s evaluation of the GPR models (10-fold CV MAE and the parity plot used to justify that the models are “reasonably accurate”) is not sufficiently reliable because the provided notebook selects and persists a “best” model based on CV test-fold performance and then uses that selected split/model for reporting and inference, which can introduce optimistic bias and undermines the robustness of the stated generalization performance.\n\n\"To further enhance the assessment of our models' reliability, we implemented 10-fold cross-validation (CV), in which the dataset is partitioned into 10 equal segments.\" \n  \n  Quote: \"The overall error is determined by averaging the errors across all ten models.\" \n  \n  Quote: \"Overall, we believe that our ML models are reasonably accurate given the size of the current training dataset.\"\nThese sentences collectively claim that the reported CV MAE provides a reliable assessment of model quality for this small dataset (28 additives plus baseline). With ~29 total samples, 10-fold CV implies each test fold contains only about 2–3 samples, so fold-to-fold error estimates can be highly variable and sensitive to which specific points fall in the test set. In such regimes, reporting only mean ± standard deviation of MAE without additional stability checks (e.g., repeated CV, or clearly separating model selection from performance estimation) can give a misleading impression of robustness. This matters because the paper uses the perceived reliability of CV performance to justify deploying the model for candidate ranking among 125 combinations. When CV is also used (implicitly or explicitly) to choose a final model, the reported error no longer cleanly estimates performance on independent data. Therefore, the paper’s conclusion about “reasonable accuracy” is not adequately supported by the described CV protocol and the way it is used downstream.\n```python\n        if mae_test < best_score:\n            best_score = mae_test\n            best_model = model\n            X_train_best[prop] = X_train\n            X_test_best[prop] = X_test\n            y_train_best[prop] = y_train\n            y_test_best[prop] = y_test\n            \n            \n\n    torch.save(best_model.state_dict(), f'best_model_{prop}.pth')\n    torch.save(likelihood.state_dict(), f'best_likelihood_{prop}.pth')\n```\nThis code shows that the notebook chooses a single “best” fold/model by minimizing the test-fold MAE (`mae_test`) within cross-validation. That is a form of model selection performed on the same held-out data used for evaluation, which breaks the separation between assessment and selection that CV error estimates rely on. Even if the manuscript reports the *average* MAE across folds, the persisted model used for later inference is chosen based on favorable test-fold outcomes, which can lead to overly optimistic downstream behavior (and can select a model that happened to do well on a small test fold by chance). Notably, the saved `best_likelihood_{prop}.pth` is written from the in-scope `likelihood` object without tracking a corresponding `best_likelihood`, so the persisted model and likelihood can come from different folds. In addition, the parity plot and error bars are generated using `X_train_best`/`X_test_best`, i.e., the “best” split, rather than aggregating out-of-fold predictions across all folds; this can visually overstate agreement. This is particularly problematic when the dataset is very small, because the variance of fold metrics is high and the best fold is not representative. As a result, both the reported visualization and the chosen saved model are entangled with test-fold performance, weakening the validity of the model assessment used to support the paper’s conclusions.\n\"We show that using CV to compute an error estimate for a classifier that has itself been tuned using CV gives a significantly biased estimate of the true error.\" [[1]](https://bmcbioinformatics.biomedcentral.com/articles/10.1186/1471-2105-7-91)\nThis statement captures a widely recognized pitfall: when CV is used to guide a choice (e.g., selecting parameters or models), the same CV error cannot be interpreted as an unbiased estimate of generalization error unless the selection procedure is nested within the evaluation. In the reviewed notebook, selecting the “best_model” by minimizing `mae_test` across folds is a direct instance of choosing based on CV test performance. The manuscript then uses CV-derived accuracy and uncertainty to justify selecting candidates for experimental validation, which amplifies the impact of any optimistic bias. While the cited result is for classification, the principle applies equally to regression workflows where hyperparameters, kernels, or models are chosen based on CV performance. Best practice in such settings is to use nested CV or an external hold-out set for final reporting and for selecting a deployable model. Without this separation, the robustness of the paper’s reported predictive performance and its downstream selection decisions is not established.\n\nReferences:\n[1] [Varma, S. & Simon, R. (2006). Bias in error estimation when using cross-validation for model selection. *BMC Bioinformatics*, 7, 91.](https://bmcbioinformatics.biomedcentral.com/articles/10.1186/1471-2105-7-91)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|32|GPT|3", "source": "prb", "split": "test", "paper_id": "prb32", "comment": "The manuscript’s conclusion that ML-identified additives “demonstrated superior performance” is not reproducible from the provided local paper/code/data bundle because the key experimental results used to support this claim (the “top 6” validation and the full 125-candidate prediction table referenced in the SI) are not present in the included datasets, preventing independent verification.\n\n\"The experimental measurements for the top 6 dual additives candidates are reported in Table 1\" \n  \n  Quote: \"Using our trained GPR models, we performed prediction of ASI, ∆ASI, and Q for 125 unknown additive candidates. The results were tabulated in as shown the SI (Spreadsheet titled “LNMO_wSingle_additive_customFeats_Highlighted.xlxs”).\"\nThese sentences indicate that the key evidence for ML-guided discovery is split between Table 1 (new experimental measurements) and an SI spreadsheet (predictions over 125 candidates). However, within the provided local review bundle, there is no supplementary directory containing the referenced SI spreadsheets, and the local code directory only includes `predictedPerformance.xlsx` (model outputs) plus the initial experimental dataset. Without the referenced SI materials, a reviewer cannot verify how candidates were ranked, what uncertainties were used, or whether the selected “top 6” corresponds to the stated ranking criteria. Moreover, Table 1’s numerical results are not accompanied by raw cycling/impedance time-series, replicate cell data, or experimental protocols sufficient to recompute the reported metrics. This prevents independent re-analysis and makes it impossible to evaluate whether the reported improvements are robust. Because these missing artifacts directly support the central claim of superior ML-identified additives, the paper’s reproducibility is substantially compromised.\n\"- _measuredPerformance.xlsx_: Experimental measurements of 28 intial additives and the baseline\" \n  \n  Quote: \"- **MLmodels.ipynb**: Jupyter notebook for training machine learning model and make predictions\" \n  \n  Quote: \"- _featGen.ipynb_: Jupyter notebook for enumerating additve combinations and generating features\" \nThis README description confirms that the only experimental spreadsheet shipped with the code is the initial dataset (28 additives plus baseline). It also implies that subsequent claims about experimentally validating “top 6” ML-selected candidates are not supported by a corresponding measurement file within the shared artifacts. In computationally assisted experimental papers, it is standard to release both the training dataset and the validation dataset (or at least the aggregated measurements used to form the reported metrics) so that independent readers can verify the improvement claim. Here, the repository structure makes clear that those validation measurements are not available locally, even though they are critical to the headline result. The absence of a validation dataset is not a minor documentation gap; it prevents any audit of whether the tested six additives were chosen as claimed and whether their measured performance truly exceeds the initial dataset. Consequently, the paper’s experimental validation claims are not reproducible from the provided materials.\n```text\nrows 29\nName,FinImpedance,DeltaImpedance,FinSpcCap\nLi2C2O4_1+MS_1,60.09,19.490000000000002,91.579\nLiBOB_1+LDF_1,54.77,15.800000000000004,92.042\nBaseline,54.47,19.35,91.942\nADM_1+LiOtC4F9_1,118.4,79.63,42.188\nLiBOB_1+LiBFEP_1,180.22,93.71,50.021\nLiDFOB_1+LiBFEP_1,111.47,53.19,66.744\nADM_1+TMSPi_1,129.23,45.849999999999994,91.47\n\ncontains LiBOB_1+SA_1? False\n```\nThis excerpt from the provided `measuredPerformance.xlsx` shows that the local experimental dataset indeed contains 29 rows (28 additives plus baseline), consistent with the manuscript’s description of the initial dataset. Critically, it also shows that the best-performing ML-validated formulation claimed in Table 1 (LiBOB 1.0 wt% + SA 1.0 wt%) is not present in this file. Therefore, none of the experimental numbers in Table 1 can be cross-checked against the provided local data, even at the aggregate-metric level. This prevents reproducing the key comparative claim that the ML-selected additive “outperformed all additives in the initial dataset,” because the purported validation results are not supplied in machine-readable form. In experimental battery research, even when only summary metrics are reported, providing the underlying tabulated measurements is essential for independent verification and reuse. The absence shown here is a direct barrier to reproducibility and materially weakens the evidentiary basis of the manuscript’s main claim.\n\"Importantly, it is our intent that the principles apply not only to ‘data’ in the conventional sense, but also to the algorithms, tools, and workflows that led to that data. All scholarly digital research objects—from data to analytical pipelines—benefit from application of these principles, since all components of the research process must be available to ensure transparency, reproducibility, and reusability.\" [[5]](https://www.nature.com/articles/sdata201618)\nThis passage articulates a now-standard expectation: reproducibility requires access not only to a paper’s narrative but also to the underlying data and the computational workflow that produced the results. In the reviewed work, the central contribution hinges on a workflow that links model training, candidate enumeration, candidate prediction, and experimental validation. Yet the local artifact set lacks the validation measurements and the referenced SI candidate-ranking table, meaning key workflow outputs are not available for review. This gap prevents independent confirmation that the workflow was executed as described and that conclusions follow from the stated evidence. The FAIR framing is directly relevant because it explicitly includes workflows and tools, not just raw measurements. By not providing the critical intermediate and validation artifacts locally, the paper falls short of widely accepted reproducibility standards for data-driven experimental studies.\n\nReferences:\n[5] [Wilkinson, M. D., Dumontier, M., Aalbersberg, I. J., et al. (2016). The FAIR Guiding Principles for scientific data management and stewardship. *Scientific Data*, 3, 160018.](https://www.nature.com/articles/sdata201618)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|32|GPT|4", "source": "prb", "split": "test", "paper_id": "prb32", "comment": "The manuscript’s claim that ML-identified additives “outperformed” the baseline and the initial dataset is not statistically well supported because Table 1 reports single-point performance metrics without stating the number of replicate cells, measurement variability, or uncertainty propagation, making it unclear whether the reported performance differences are robust.\n\n\"The additives generated through this ML approach demonstrated superior performance compared to those in the initial dataset.\" \n  \n  Quote: \"More importantly, the addition of either MS or SA to LiBOB show notable enhancement in all three considered metrics, with the combination of LiBOB at 1.0 wt% and SA at 1.0 wt% achieving the highest final specific capacity (95.49 mAhg⁻¹) among all additives in this work.\"\nThese statements are strong comparative claims that depend on the magnitude of performance differences relative to experimental variability. In Table 1, the claimed best formulation has Q = 95.49 mAhg⁻¹ versus the baseline Q = 91.94 mAhg⁻¹, a difference of ~3.6 mAhg⁻¹; without replicate information it is impossible to judge whether this is outside typical cell-to-cell scatter for this test protocol. The same issue applies to impedance metrics, where differences of only a few Ω·cm² can be within measurement variability depending on EIS fitting and cell history. Because the paper uses these differences to argue successful ML-guided discovery, the uncertainty around each metric is essential to evaluate the robustness of the conclusion. Reporting only point estimates forces readers to assume negligible variability, which is rarely justified in electrochemical cell testing. Therefore, the conclusion of “superior performance” is not adequately supported by the reported statistical treatment.\n```text\n| 32 | LiBOB 1.0 wt% + SA 1.0 wt% | 46.79 | 10.19 | 95.49 |\n|   | Baseline | 54.47 | 19.35 | 91.94 |\n```\nThis excerpt from Table 1 provides only single-point summary values for the best-performing formulation and the baseline. There is no reported number of replicate cells (*n*), no dispersion metric (e.g., standard deviation), and no description of how these point values were aggregated from potentially time-dependent EIS/cycling measurements. Without replicates, it is impossible to determine whether the observed differences (e.g., Q and impedance metrics) are robust or could be driven by cell-to-cell variability, fitting choices, or experimental noise. This omission is particularly consequential because the manuscript’s central comparative conclusion is based on ranking these point estimates across formulations. Standard practice in electrochemical performance reporting is to provide replicate statistics or, at minimum, clarify measurement variability and how key metrics were computed. As presented, Table 1 does not contain sufficient statistical information to support a strong “outperformance” claim.\n\"The error bars indicate one standard deviation.\" \nThis statement (Fig. 5 caption) specifies that error bars are one standard deviation, but it does not clarify whether this refers to experimental replication, cross-validation variability, or model predictive uncertainty. The provided notebook suggests these error bars are model predictive uncertainties, which are conceptually different from experimental measurement error and cannot substitute for replicate testing. Without explicitly distinguishing these uncertainty sources, readers may incorrectly interpret model uncertainty as experimental reproducibility. In battery studies, measurement uncertainty and sample-to-sample variation are often the limiting factors when claiming improvements, so conflating uncertainty types undermines interpretability. Moreover, even if model uncertainty is shown, it does not establish that measured improvements are statistically significant. This ambiguity limits the strength of the paper’s comparative conclusions.\n\"The summary statistics shown in bar graphs, line graphs, and box plots are only meaningful when there are enough data to summarize.\" [[4]](https://journals.plos.org/plosbiology/article?id=10.1371/journal.pbio.1002128)\nWhile this perspective focuses on biological data presentation, its core point applies directly here: without knowing how many independent observations underlie each reported metric, summary statistics (or single values) cannot be interpreted as robust evidence. In the reviewed manuscript, Table 1 gives single ASI/∆ASI/Q values per formulation and does not report replicate counts or dispersion, so the reader cannot assess whether the observed ordering is stable. This is particularly important because the claimed improvements are modest in absolute terms for some metrics, and battery performance can vary across nominally identical cells. Good practice would include reporting *n* (number of cells), dispersion (e.g., SD), and how summary metrics were computed from raw time series. Without such reporting, the comparative conclusions about “outperformance” remain under-justified. Therefore, the statistical support for the paper’s key experimental claim is insufficient.\n\nReferences:\n[4] [Weissgerber, T. L., Milic, N. M., Winham, S. J., & Garovic, V. D. (2015). Beyond Bar and Line Graphs: Time for a New Data Presentation Paradigm. *PLOS Biology*, 13(4), e1002128.](https://journals.plos.org/plosbiology/article?id=10.1371/journal.pbio.1002128)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|32|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb32", "comment": "The machine learning pipeline contains a critical implementation error where the data scaler fitted on the last cross-validation fold is applied to the final model selected from the best fold, leading to incorrect predictions on the unknown dataset.\n\n```python\n    # Loop over folds\n    for train_index, test_index in kf.split(X):\n        # ...\n        # Scale the data\n        sc = StandardScaler()\n        X_train = sc.fit_transform(X_train)\n        # ...\n        if mae_test < best_score:\n            best_score = mae_test\n            best_model = model\n            # ...\n```\nThe code iterates through 10 folds. In each iteration, a new `StandardScaler` (`sc`) is fitted to the training data of that specific fold. The `best_model` is saved whenever a fold achieves a lower MAE. However, the `sc` variable is overwritten in each iteration and persists after the loop finishes, holding the state of the *last* fold's scaler.\n```python\n    # Make predictions on unknown dataset  \n    X_newAdd = sc.transform(dfEnumFeats)\n```\nWhen predicting on the unknown dataset (`dfEnumFeats`), the code uses `sc` (from the last fold) to transform the features. If the `best_model` was selected from any fold other than the last one (which is highly probable), there is a mismatch between the scaler used for training the model and the scaler used for inference. This means the model receives input data that is scaled with the wrong mean and standard deviation, rendering the predictions mathematically invalid and effectively random.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|32|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb32", "comment": "The dataset size (29 samples) is insufficient for the high-dimensional feature space (27 features), leading to a high risk of overfitting and unreliable generalization.\n\n\"In this study, we selected and tested a diverse collection of 28 single and dual additives\"\nThe initial dataset consists of only 28 additives (plus a baseline). This is an extremely small dataset for machine learning applications.\n```python\nShape: (29, 30)\nFeatures: ['O_1', 'C_3_inRing', 'O_2_inRing', 'B[-1]_4_inRing', 'F_1', 'Li[+1]', 'C_2_inRing', 'B_3_inRing', 'C_1', 'C_2', 'N_2_inRing', 'N_3_inRing', 'C_3', 'O[-1]_1', 'N[+1]_4_inRing', 'S_4_inRing', 'P[-1]_4', 'Si_4', 'O_2', 'P_3', 'P[-1]_6_inRing', 'P_4', 'C_4', 'S_4', 'N_2', 'aromaticRing', 'aliphaticRing']\n```\nThe code analysis reveals that 27 distinct features are used to describe these 29 samples. In machine learning, a rule of thumb is to have at least 10 times as many samples as features to avoid the \"curse of dimensionality\" [1]. With a ratio of nearly 1:1, the model can easily overfit the training data, even with Gaussian Process Regression. The reported cross-validation metrics are likely optimistic due to the small sample size in each fold (approx. 3 samples), making the model's ability to generalize to the 125 unknown additives highly questionable.\n\nReferences:\n[1] Liu, Z. et al. A framework for data-driven analysis of materials under uncertainty: Countering the curse of dimensionality. *Computer Methods in Applied Mechanics and Engineering* **320**, 633-658 (2017).", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|32|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb32", "comment": "The paper claims a synergistic effect for the discovered binary additive (LiBOB + SA) but fails to compare it against LiBOB alone, making it impossible to attribute the performance to the combination.\n\n\"we discovered a new binary formulation, namely LiBOB at 1wt% and SA at 1wt%, that outperformed all additives in the initial dataset.\"\nThe initial dataset includes SA (Succinic Anhydride) as a single additive but does not include LiBOB as a single additive (only in combinations). LiBOB is a well-known and effective electrolyte additive for high-voltage cathodes [2]. Without a control experiment using LiBOB alone at 1wt% or 2wt%, it is scientifically unsound to claim that the superior performance is due to the *binary* combination or \"synergy\". It is entirely possible that LiBOB alone would achieve similar or better performance.\n\"In this work, the dual additives always consist of a cathode and an anode additive each, as we hypothesized that their co-existence in the electrolyte and the synergistic effects would be critical\"\nThis hypothesis remains unproven for the top candidate because the individual contribution of LiBOB was not isolated.\n\nReferences:\n[2] Xu, K. Electrolytes and interphases in Li-ion batteries and beyond. *Chemical Reviews* **114**, 11503-11618 (2014).", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|32|Gemini|5", "source": "prb", "split": "test", "paper_id": "prb32", "comment": "The feature engineering approach, based primarily on atomic counts and coordination, is too simplistic to capture the complex chemical interactions and degradation mechanisms in high-voltage electrolytes.\n\n\"The assignment of the descriptors/features for additives here is inspired by the previous work of Okamoto et al, wherein the frequency/count of each atom and its coordination in the structure was tabulated.\"\nThe features used are simple counts of atoms and functional groups (e.g., \"B[-1]_4_inRing\"). These descriptors fail to capture critical physicochemical properties such as HOMO/LUMO energy levels, dipole moments, reduction/oxidation potentials, or steric effects, which are essential for understanding SEI/CEI formation [3]. More advanced descriptors derived from Density Functional Theory (DFT) or molecular fingerprints are standard in modern materials informatics to provide a physical basis for the model's predictions [4]. The lack of chemically meaningful features limits the model's ability to learn true structure-property relationships.\n\nReferences:\n[3] Zhang, Y. & Xu, X. Machine Learning Properties of Electrolyte Additives: A Focus on Redox Potentials. *Industrial & Engineering Chemistry Research* **60**, 343–354 (2021).\n[4] Doan, H. A. et al. Quantum Chemistry-Informed Active Learning to Accelerate the Design and Discovery of Sustainable Energy Storage Materials. *Chemistry of Materials* **32**, 6338–6346 (2020).", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|32|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb32", "comment": "The authors used the parameters of area specific impedance (ASI), area impedance rise (∆ASI), and final specific capacity (Q) to evaluate the additives for electrolytes design. If other parameters could be employed or the parameters affect the machine learning model? There is an inter-correlation between the three indicators (specific impedance (ASI), impedance rise (∆ASI), and final specific capacity (Q)) chosen by the authors. Does this correlation have an impact on the model?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|32|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb32", "comment": "The well-formed descriptors are the basis for implementing machine learning models, and the authors specifically introduced \\\"rings\\\" as part of the descriptors. What are the benefits of this improved approach?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|32|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb32", "comment": "The authors experimentally tested the effects of 28 additives in relatively small amount. Does the machine learning model fall into local optimal solutions? How well does the model scale up to other electrolyte additive systems?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|32|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb32", "comment": "The authors used Gaussian Process Regression (GPR) regression method. Can other regression methods be used for training and is GPR optimal among the various methods?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|32|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb32", "comment": "The fitted convergence curves for machine learning need also to be provided to analyze the convergence effect.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|32|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb32", "comment": "The initial dataset of 28 samples is too small for training the machine learning model due to potential overfitting issues. Although 10-fold cross-validation was performed, the fixed train-test set limits the robustness of the model. It is recommended to use 5-fold cross-validation and also vary the train-test ratio from 2:8 to 8:2 with at least 10 different random states to better validate the model's performance. In addition, the performance of various types of ML algorithms should be provided.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|32|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb32", "comment": "The study appears to use exploitation to validate the ML model's predictive capability with 128 sets. However, Bayesian based active learning, which is more effective and has been confirmed its validity from various researches, should be considered for the optimization process.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|32|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb32", "comment": "The rationale for using ML in this study is unclear. While conducting 128 experiments is time-consuming and costly, the search space is relatively small from an ML perspective. The authors should justify that 128 sets are sufficient and that the best result is included. A more rigorous search and justification for the additive combinations are needed. It seems conducting 128 experiments would be more effective.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|32|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb32", "comment": "The extrapolation performance of the ML model should be validated, as ML models are typically weak in this area. Dimensionality reduction techniques should be applied to both train (28) and test (128) sets to understand the ML search space and determine whether it involves extrapolation or interpolation.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|32|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb32", "comment": "The authors should demonstrate that the optimal set of additives is also effective for different chemical compositions of LNMO (e.g., LiNi0.6Mn1.4O4 or LiNi0.5Mn1.4Dopant0.1O4), as the tested LNMO composition may not be the best cathode material.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Claude|1", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "Table 1 reports \"R²\" values for binary classification tasks (solid/liquid classification and conductivity σ ≥ 5 or σ < 5 classification), which is fundamentally incorrect since R² is a regression metric, not a classification metric. The footnote attempts to clarify this as \"5-fold cross-validation accuracy results,\" but this creates confusion between two mathematically distinct metrics.\n\n\"| Algorithm | R² (Solid or Liquid) | R² (σ ≥ 5 or σ < 5) | ... | Support Vector Machine (SVM) | 0.80 | 0.82 | ... | Random Forest (RF) | 0.85 | 0.81 | ... | XGBoosting (XGB) | 0.86 | 0.81 | ... | Graph Convolutional Neural Network (GCN) | 0.83 | NA |\"\nThe table header explicitly labels the metric as \"R²\" for classification tasks. R² (coefficient of determination) is defined as the proportion of variance explained in regression problems and ranges from negative infinity to 1, while classification accuracy is the proportion of correct predictions and ranges from 0 to 1. Using R² terminology for classification results misrepresents the evaluation methodology and could mislead readers about the actual model performance metrics used.\n\"*The R² for SVM, RF and XGB algorithms are the average of the 5-fold cross-validation accuracy results.\"\nThis footnote confirms that the authors actually measured accuracy but mislabeled it as R². The standard machine learning practice distinguishes clearly between regression metrics (R², MSE, MAE) and classification metrics (accuracy, precision, recall, F1, AUC-ROC). This terminology error undermines the scientific rigor of the methodology reporting.\n\"True and false positives and negatives are used to calculate several useful metrics for evaluating models... Accuracy: Given a balanced dataset, with similar numbers of examples in both classes, accuracy can serve as a coarse-grained measure of model quality.\" [[1]](#citation-1)\nStandard machine learning resources clearly distinguish classification metrics from regression metrics. The Google Machine Learning guide specifically describes accuracy as being calculated from true/false positives and negatives—fundamentally different from R² which measures variance explained. Proper classification evaluation should also report precision, recall, F1-score, or AUC-ROC, none of which are provided in the paper.\n\nReferences:\n[1] [Google Machine Learning Crash Course: Classification Metrics](https://developers.google.com/machine-learning/crash-course/classification/accuracy-precision-recall)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Claude|2", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "The paper uses DFT-computed electrochemical window (ECW) values from HOMO/LUMO calculations as a critical screening criterion (ECW > 3.5 V), but the validation data reveals a negative R² score (-5.53) and systematic overestimation with mean absolute error of 1.58 V and mean relative error of 38.4%, rendering this criterion unreliable for ionic liquid screening.\n\n\"The last screening step is determined by the computed electrochemical window value (ECW) according to Eq. 1–3 through Psi4.\"\nThe paper presents ECW computation as a definitive screening criterion. However, analysis of the paper's own validation data (ECW_valid.csv) reveals severe prediction errors. The computed ECW systematically overestimates experimental values by an average of 1.42 V, with 91.3% of predictions being overestimates. For example, 1-Ethyl-3-methylimidazolium tetrafluoroborate shows experimental ECW of 3.6 V versus computed 8.62 V—a 5.0 V discrepancy that fundamentally undermines the use of a 3.5 V threshold.\n\"Finally, we propose 40 ILs with σ ≥ 5 mS cm⁻¹ along with an satisfactory ECW > 3.5 V in the final recommendation list for development of IPE in LMBs.\"\nGiven the demonstrated systematic overestimation of ECW values (mean bias +1.42 V, R² = -5.53), an IL with computed ECW just above 3.5 V could easily have an actual ECW around 2 V, which would be insufficient for lithium metal battery applications requiring stability against Li/Li⁺ redox potential. The negative R² indicates that the computed ECW predictions are worse than simply using the mean experimental value.\n\"The ECW of an IL is determined by both cations and anions. The cathodic limit (V_CL) is the maximum value of the cathodic potential determined by the E_LUMO for cations and anions. Similarly, the anodic limit (V_AL) is the minimum value of the anodic potential determined by the E_HOMO for cations and anions.\"\nWhile the theoretical basis from Ong et al. [[2]](#citation-2) provides a foundation for estimating ECW from orbital energies, the actual predictive performance in this study falls far short of what would be required for reliable materials screening. The method may work for relative ranking but not for absolute threshold-based filtering as employed here.\n\nReferences:\n[2] Ong, S. P., Andreussi, O., Wu, Y., Marzari, N. & Ceder, G. Electrochemical Windows of Room-Temperature Ionic Liquids from Molecular Dynamics and Density Functional Theory Calculations. *Chem Mater* **23**, 2979–2986 (2011). https://doi.org/10.1021/cm200679y", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Claude|4", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "The paper reports only accuracy-type metrics for classification tasks without providing precision, recall, F1-score, or confusion matrices, which are essential for evaluating binary classifiers, especially when class distributions may be imbalanced.\n\n\"The efficiencies of employed models are included in Table 1. We observe that the GCN model offers similar performance only based on the chemical geometric descriptors without any additional calculation results.\"\nTable 1 provides only a single metric per classification task (mislabeled as R²). Standard practice in machine learning classification requires reporting multiple complementary metrics. Accuracy alone can be misleading, particularly if class distributions are imbalanced—for example, if 80% of ILs are naturally liquid at room temperature, a model predicting all ILs as liquid would achieve 80% accuracy without learning anything meaningful.\n\"In an imbalanced dataset where the number of actual positives is very low, recall is a more meaningful metric than accuracy because it measures the ability of the model to correctly identify all positive instances.\" [[1]](#citation-1)\nMachine learning best practices emphasize that accuracy alone is insufficient for classifier evaluation. The paper provides no information about class distributions in the training data, precision (how many predicted liquid ILs are actually liquid), or recall (what fraction of actual liquid ILs were correctly identified). Without these metrics, readers cannot assess whether the model has systematic biases in prediction.\n\"Metrics like precision, recall, and MCC are better suited to these scenarios but are underutilized in business data mining applications.\" [[3]](#citation-3)\nRecent literature specifically highlights that accuracy is often an inappropriate sole metric for classification evaluation. The Matthews Correlation Coefficient (MCC) is particularly recommended for binary classification as it accounts for all four quadrants of the confusion matrix and provides a balanced measure even with imbalanced datasets.\n\nReferences:\n[1] [Google Machine Learning Crash Course: Classification Metrics](https://developers.google.com/machine-learning/crash-course/classification/accuracy-precision-recall)\n[3] [Springer Journal of Big Data: Accuracy, precision, recall, f1-score, or MCC? empirical study](https://link.springer.com/article/10.1186/s40537-025-01313-4)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Claude|5", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "The GCN model uses a simple 80/20 train-test split for validation rather than cross-validation, limiting the statistical reliability of the reported 0.83 accuracy and contrasting with the 5-fold cross-validation applied to other models.\n\n* Quote from code (lines 961-972):\n```python\ntrain_start = 0\ntrain_end = round(len(train_dataset) * 0.8)\nfactor = pd.factorize(train_dataset['state'], sort=True)\ntrain_dataset['state'] = factor[0]\n\ntrain_x_smiles = list(train_dataset['pair_sml'].iloc[train_start:train_end])\ntrain_y = list(train_dataset['state'].iloc[train_start:train_end])\nval_x_smiles = list(train_dataset['pair_sml'].iloc[train_end:])\nval_y = list(train_dataset['state'].iloc[train_end:])\n```\nThe GCN model implementation uses a single random 80/20 split for training and validation, whereas the paper reports \"5-fold cross-validation accuracy results\" for SVM, RF, and XGB models. This methodological inconsistency means the GCN accuracy has higher variance and may not be directly comparable to the other models' performance metrics.\n\"The R² for SVM, RF and XGB algorithms are the average of the 5-fold cross-validation accuracy results.\"\nThis footnote confirms that cross-validation was performed for traditional ML models but the code shows GCN uses only a single split. Cross-validation provides more robust performance estimates by averaging across multiple train/test partitions, reducing the impact of a particular random split on the reported performance.\n\"Cross-validation determines the accuracy of your machine learning model by partitioning the data into two different groups... Performance evaluation in cross-validation refers to assessing a model's predictive performance on different subsets of training data.\" [[4]](#citation-4)\nCross-validation is standard practice for reliable model evaluation, especially with limited datasets. The ionic liquid dataset appears small enough that single-split evaluation could produce highly variable accuracy estimates depending on which samples end up in training versus test sets.\n\nReferences:\n[4] [Coursera: What Is Cross-Validation in Machine Learning?](https://www.coursera.org/articles/what-is-cross-validation-in-machine-learning)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|GPT|1", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "The machine-learning dataset construction applies a physically unjustified temperature normalization for ionic-liquid conductivity/viscosity/density, which can systematically corrupt the “room-temperature” labels and features used for screening ILs.\n\n“This method processes the crawled data, including the ion types and the ionic conductivity, the viscosity and the density of the ionic liquids. The properties are all normalized to 25°C.”\nThis establishes that temperature normalization is not an incidental implementation choice but a core dataset transformation. Because the paper’s screening logic is explicitly based on room-temperature phase and room-temperature conductivity categories, any systematic normalization error propagates directly into the training labels and screening thresholds. In small-data ML (which the manuscript emphasizes), label/feature corruption can dominate model error and lead to spurious “golden rules.” In common practice, temperature normalization of transport properties requires a physically motivated model (e.g., Arrhenius/VFT fits) or restricting to measurements at a consistent temperature. A blanket normalization to 25°C without a justified functional form risks reordering candidates, directly affecting which ILs enter the recommendation list. This is therefore a validity-critical issue, not merely a documentation gap.\n```python\n# When the test temperature is NaN, set the test temperature to 25°C\ndataset[['T_conductivity', 'T_density', 'T_viscosity']] = dataset[\n    ['T_conductivity', 'T_density', 'T_viscosity']].fillna(self.T_norm)\n\n# Get the 'conductivity', 'viscosity', and 'density' at room temperature（25°C）\n\n# If 'conductivity_norm', 'viscosity_norm', 'density_norm' is 0, then assign to None\ndataset['conductivity_norm'] = dataset['conductivity'] / dataset['T_conductivity'] * self.T_norm\ndataset['viscosity_norm'] = dataset['viscosity'] / dataset['T_viscosity'] * self.T_norm\ndataset['density_norm'] = dataset['density'] / dataset['T_density'] * self.T_norm\n```\nThis code linearly rescales each property by multiplying by (25 / T_measured), which implicitly assumes the property varies linearly with temperature and passes through the origin. That assumption is not generally correct for ionic conductivity or viscosity in ionic liquids, where temperature dependence is commonly exponential (Arrhenius-like) or VFT/VTF-like rather than linear. Additionally, imputing missing measurement temperatures as 25°C makes the normalized value equal to the reported value even when the original temperature is unknown, silently introducing mislabeled “room-temperature” datapoints. Because downstream classification uses a hard threshold at 5 mS cm⁻¹, even moderate normalization errors can flip class labels and alter the recommendation list. The method therefore risks producing systematically incorrect screening outcomes even if the ML model itself were perfect. This directly undermines validity.\n“Among the 2356 ILs, we initially use the classification method to predict the state (solid/liquid) of the ion pairs at RT. Then we employ both statistical regression and classification to evaluate the conductivity of the obtained 1240 ILs (liquid at RT).”\nThis passage makes explicit that the workflow’s targets are room-temperature phase and room-temperature conductivity. Therefore, any mapping from heterogeneous-temperature measurements into a single “RT” label is central to the method’s correctness. If the RT proxy is biased, then the reported intermediate counts (e.g., 1240 liquid ILs) and the final screened list are not reliable. This also weakens the experimental-validation narrative because experimental selection is conditioned on the screen’s RT-based outputs. In materials screening, it is standard to either use consistent-temperature measurements or apply a physically motivated temperature model when converting between temperatures. The presented linear normalization does not meet that standard.\n“However, a significant decrease in conductivity is observed upon cooling, following a characteristic Vogel-Fulcher-Tammann (VFT) temperature dependence” [5](#ref5)\nThis peer-reviewed reference illustrates that conductivity in ionic-liquid(-crystal) systems is commonly treated as non-linear in temperature, here explicitly VFT-like. The key point is not that every IL follows exactly VFT, but that established practice does not assume a linear proportionality σ ∝ T. Because the manuscript’s code uses a one-size-fits-all linear temperature ratio, it is not aligned with this common physical picture. That mismatch implies the pipeline’s 25°C-normalized conductivity values can be systematically wrong, especially for materials measured far from 25°C. Consequently, the ML screening is built on potentially distorted targets and features. This undermines the validity of the screening conclusions.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|GPT|2", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "The supervised-learning evaluation is reported with inconsistent metrics and is implemented with leakage-prone validation (preprocessing fit outside cross-validation and non-nested tuning), making the stated model performance and screening reliability untrustworthy.\n\n“| Algorithm | R<sup>2</sup> (Solid or Liquid) | R<sup>2</sup> (σ ≥ 5 or σ &lt; 5) |\n|---------|-------------------------------|-------------------------------|\n| Support Vector Machine (SVM) | 0.80 | 0.82 |\n| Random Forest (RF) | 0.85 | 0.81 |\n| XGBoosting (XGB) | 0.86 | 0.81 |\n| Graph Convolutional Neural Network (GCN) | 0.83 | NA |\n\n*The R<sup>2</sup> for SVM, RF and XGB algorithms are the avergae of the 5-fold cross-validation accuracy results.”\nThis table labels the metric as R² but describes it as “cross-validation accuracy,” which are different quantities and not interchangeable. For the paper’s binary classification tasks (solid vs liquid; σ ≥ 5 vs σ < 5), accuracy and ROC-AUC (plus calibration) are standard, whereas R² is a regression metric and atypical for classification. The inconsistency prevents readers from understanding what was optimized and what the reported values actually represent. Because these numbers justify the screening approach (i.e., the model is “good enough” to recommend ILs), ambiguity here directly affects the credibility of the conclusions. In materials-ML practice, clear separation of regression vs classification metrics is essential to interpret model reliability and compare against prior work. As written, the evaluation reporting is not sufficiently reliable.\n```python\n# Normalize the train set and pred_data\nscaler = MinMaxScaler(feature_range=(0, 1))\nscaler.fit(train)\ntrain = scaler.transform(train)\n\n# K-fold validation of the model\nkf = KFold(n_splits=5)\nscore = cross_val_score(clf, X_train, y_train, cv=kf)\n```\nThe scaler is fit once on the full supervised dataset and then reused for all folds in cross-validation, which leaks information from each validation fold into the learned preprocessing transformation. This leakage can inflate cross-validated performance, particularly in small chemistry datasets where scale/shift can encode dataset-wide structure. Standard practice is to fit preprocessing only on each fold’s training partition (e.g., by wrapping scaler + model in a pipeline) so that the validation fold remains truly unseen. The code also uses KFold without stratification for classification, which can yield unstable folds if class balance is uneven. As a result, the cross-validation scores are not a reliable estimate of generalization to new ionic liquids. This undermines the screening claims.\n“The general rule is to never call fit on the test data.” [1](#ref1)\nThis guidance from the scikit-learn documentation directly applies because each CV validation fold is effectively a “test” set for that fold. Fitting the scaler before cross-validation violates the rule by letting validation data influence a learned transformation, producing overly optimistic scores. Even when the leakage is subtle, it can be enough to change rankings when models are used for candidate selection rather than only for prediction. Since the manuscript uses these models to drive a screening funnel, optimistic performance estimates can waste experimental resources and give false confidence in “recommended” ILs. The documentation also emphasizes that transformations must be “only learnt from the training data,” which the current implementation does not guarantee. Therefore, the reported performance is not a trustworthy basis for the paper’s screening conclusions.\n“We show that using CV to compute an error estimate for a classifier that has itself been tuned using CV gives a significantly biased estimate of the true error.” [2](#ref2)\nThe workflow performs hyperparameter tuning (e.g., via GridSearchCV) and then reports cross-validation performance without a clearly nested evaluation separating tuning from assessment. Varma & Simon show that this setting can bias error estimates downward unless nested CV or an independent holdout test set is used for final reporting. This is particularly relevant here because the manuscript stresses “robust” screening under data scarcity, where biased validation is a known failure mode. A standard remedy would be nested cross-validation for any performance claims used to justify screening decisions, or a final untouched test set at the level of unique IL identities. Without such precautions, the model quality claims and the robustness of the screening funnel are not well supported. This affects both validity and conclusions.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|GPT|3", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "The screening step treats a vacuum HOMO/LUMO-derived electrochemical window (ECW) proxy as a decisive threshold (ECW > 3.5 V) without calibration or quantified uncertainty, despite acknowledging systematic overestimation, undermining the validity of the final recommendation list.\n\n“The last screening step is determined by the computed electrochemical window value (ECW) according to Eq. 1–3 through Psi4.\n\n$$\n{V}_{CL}=\\text{max}\\left(-\\frac{{E}_{LUMO}[+]}{e},-\\frac{{E}_{LUMO}[-]}{e}\\right)\n$$\n\n$$\n{V}_{AL}=\\text{min}\\left(-\\frac{{E}_{HOMO}[+]}{e},-\\frac{{E}_{HOMO}[-]}{e}\\right)\n$$\n\n$$\n\\text{E}\\text{C}\\text{W}= {V}_{AL}- {V}_{CL}\n$$\n”\nThese excerpts show that ECW is computed directly from isolated-ion orbital energies and then used as the final screening gate. While HOMO/LUMO heuristics can provide qualitative trends, using them as a hard volt-scale cutoff implicitly assumes quantitative accuracy across diverse ion chemistries. The manuscript does not provide a calibration against experimentally measured ECWs, an error model, or a sensitivity analysis showing how often the ECW threshold misclassifies candidates. In screening workflows, a hard threshold is only defensible if the proxy is validated to be conservative or if its false-positive/false-negative rates are characterized. Without that, the ECW filter can eliminate viable candidates or pass unstable ones, directly affecting the correctness of the “40 ILs” recommendation list. This is a validity issue because ECW is a headline screening objective.\n“However, both BF  \n<sub>4</sub>  \n<sup>−</sup> and Ethyl Sulfate display fluctuate current starting from 4V for BF  \n<sub>4</sub> and 3.5V for Ethyl Sulfate, which are lower compared to the computed ECWs.\n\nAs reported previously, the calculated anodic limits for BF  \n<sub>4</sub>  \n<sup>−</sup> are usually overestimated using the vacuum calculation model compared to the experimental results.”\nThe manuscript explicitly reports a mismatch between computed ECW and experimental anodic stability, and attributes it to overestimation by a “vacuum calculation model.” This is critical because the ECW>3.5 V threshold is described as the final step that determines the recommendation list. If the computation systematically overestimates anodic limits, then ECW-based thresholding is biased toward false positives, weakening the claim that screened ILs have “wide electrochemical window.” The mismatch occurs near the same voltage scale used for the cutoff, where small errors materially change pass/fail decisions. Common practice would be to calibrate the computational proxy against consistent experimental measurements or to adopt a liquid-phase ECW prediction scheme for comparable context. Without such calibration, the ECW screen is not a robust basis for the conclusions.\n“ECW values sensitively depend on experimental setup and conditions.” [3](#ref3)\nThis external reference emphasizes that ECW is context-dependent, which is precisely why uncalibrated, context-free proxies are risky as decisive screening criteria. The manuscript’s ECW model does not explicitly control for electrode/material and measurement context, yet it treats the resulting number as a hard criterion. Even if HOMO/LUMO-based proxies correlate with trends, their quantitative mapping to experimental ECW can shift with conditions, requiring validation in the intended context. Without reporting how their computed ECWs relate to a consistent experimental protocol, the paper cannot justify a universal 3.5 V cutoff. This undermines the reliability of the final recommendation list and weakens downstream claims about “wide electrochemical window” materials. The issue affects validity because ECW is a primary screening target.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|GPT|4", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "The paper interprets coulombic efficiencies exceeding 100% as evidence of high reversibility without providing uncertainty quantification or measurement-validation details, weakening the reliability of the full-cell performance conclusions.\n\n“The major population of the CE is between 100.1% – 100.2%, which is slightly higher than the theoretical maximum value (100%) because of the thermal fluctuation at the ambient temperature. Thus indicates the high reversibility of the Li metal cells based on this IPEs at RT.”\nThis sentence acknowledges CE values above the theoretical maximum, yet immediately treats them as confirming high reversibility. A CE greater than 100% means the measured discharge capacity exceeds the measured charge capacity for that cycle, which cannot be interpreted as “better-than-perfect” efficiency. Such overshoots can occur from measurement noise, drift, or definitional issues (integration limits, cutoff handling), but the magnitude must be quantified and propagated into uncertainty bounds. Attributing the effect to “thermal fluctuation” without reporting the temperature stability, current/voltage measurement precision, or replicate variability does not support the inference that the cells are highly reversible. In electrochemical studies, unusually high CE claims require careful uncertainty accounting because systematic errors of order 0.1% can dominate. Without that, the full-cell CE-based conclusions are not robust.\n“With LiFePO₄ loading ~ 10.3 mg cm⁻², the full cells deliver outstanding capacity retention for > 350 cycles (> 96% with 0.5 C at RT; > 80% with 2 C at 50 °C), fast charge/discharge capability (146 mAh g⁻¹ with 5 C at 80 °C) and ultrahigh coulombic efficiency (> 99.92%).”\nThe abstract frames CE as a headline performance metric and uses it to argue exceptional stability and practicality. When CE is used to support claims about interface stability and dendrite suppression, the required measurement precision is extremely high, and the analysis must separate real efficiency from systematic measurement artifacts. The manuscript does not specify, in the main text, the number of independent cells, confidence intervals, or how CE was computed (e.g., whether formation cycles are excluded, or how capacity integration is handled). The later statement that CE routinely exceeds 100% indicates that measurement uncertainties are non-negligible on the scale relevant to “>99.92%” claims. Standard reporting would include replicate statistics and explicit uncertainty sources when presenting unusually high CE. Without those, the abstract-level conclusions are not sufficiently supported.\n“Coulombic efficiency, defined as the ratio of discharge capacity to charge capacity, within each cycle was calculated” [4](#ref4)\nThis definition makes clear that CE is a ratio of two measured quantities and is therefore sensitive to systematic and random errors in either numerator or denominator. If the ratio routinely exceeds 1.0 (100%), the correct interpretation is not increased reversibility but inconsistent capacity accounting within the reported uncertainty. Therefore, claiming CE>100% due to thermal fluctuation requires quantitative uncertainty bounds showing that the 0.1–0.2% overshoot lies within expected error from temperature/control drift and measurement precision. Without such quantification (and ideally replicate statistics), the paper’s inference that these CE traces demonstrate extraordinary reversibility is not well supported. This is especially important because CE is used as a primary metric to benchmark performance against prior literature. The missing uncertainty treatment weakens the reliability of the conclusions.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "The paper's machine learning methodology lacks a rigorous validation protocol, specifically failing to employ an independent, held-out test set for final performance evaluation, and suffering from data leakage where the validation set is used for both training monitoring and reporting results.\n\n```python\ntrain_dataset = train_dataset.sample(len(train_dataset), random_state=1)\ntrain_start = 0\ntrain_end = round(len(train_dataset) * 0.8)\n...\ntrain_x_smiles = list(train_dataset['pair_sml'].iloc[train_start:train_end])\nval_x_smiles = list(train_dataset['pair_sml'].iloc[train_end:])\n...\nfor epoch in range(1000):\n    ...\n    acc = evaluate_model(val_data_list, gnn_model)\n    epoch_accuracy.append(acc)\n\n# Evaluate the mode\nacc = evaluate_model(val_data_list, gnn_model)\nprint(acc)\n```\nThe code demonstrates that the dataset is split only into training (80%) and validation (20%) sets using a simple random split. There is no separate test set reserved for the final evaluation. Crucially, the validation set (`val_data_list`) is used to monitor accuracy at every epoch during the 1000-epoch training loop. Reporting the final accuracy on this same validation set constitutes data leakage, as the model's performance is not being assessed on truly unseen data. In standard machine learning practices, a three-way split (train/validation/test) or nested cross-validation is required to prevent overfitting to the validation set and to provide an unbiased estimate of generalization performance.\n\"Best practices in machine learning for chemistry\" [1]\nThis reference emphasizes the necessity of an independent test set that is never used during model training or hyperparameter tuning to ensure the reported metrics reflect the model's ability to generalize to new chemical structures.\n\nReferences:\n[1] Artrith, N., Butler, K.T., Ceder, G. et al. Best practices in machine learning for chemistry. Nat. Chem. 13, 505–508 (2021). https://doi.org/10.1038/s41557-021-00716-z", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "The implementation of the Graph Convolutional Neural Network (GCN) contains fundamental methodological flaws, including the use of Mean Squared Error (MSE) loss for a binary classification task and the absence of a sigmoid activation function at the output layer.\n\n```python\n# define loss function\nloss_function = torch.nn.MSELoss()\n...\nloss_function_value = loss_function(output[:, 0], torch.tensor(batch.y, dtype=torch.float32))\n```\nThe code uses `MSELoss` for a binary classification problem (solid vs. liquid), which is methodologically incorrect. The standard loss function for binary classification is Binary Cross-Entropy (BCE). MSE is designed for regression tasks and does not penalize misclassifications in a probabilistic manner appropriate for categorical outcomes.\n```python\nself.classifier = Linear(4, 1)\n...\nout = self.classifier(out)\nreturn emb, out\n```\nThe model architecture ends with a linear layer without a sigmoid or softmax activation function. Consequently, the model outputs unbounded real numbers rather than probabilities between 0 and 1. This makes the interpretation of the output as a classification score arbitrary and unstable, as evidenced by the use of `yhat.round()` in the evaluation function without ensuring the outputs are within the [0, 1] range.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "The screening criterion based on the DFT-calculated Electrochemical Window (ECW) is unreliable due to significant discrepancies between the computed values and experimental data, which the paper fails to adequately address or validate.\n\n```csv\n1-Hexyl-3-methylimidazolium tetrafluoroborate,...,5.1,8.7009536\n1-Butyl-3-methylimidazolium tetrafluoroborate,...,4.68,8.6859392\n1-Ethyl-3-methylimidazolium tetrafluoroborate,...,3.6,8.6201424\n```\nThe `ECW_valid.csv` file generated by the authors' code reveals massive discrepancies between the experimental ECW (e.g., 3.6 V) and the computed ECW (e.g., 8.62 V) for tetrafluoroborate-based ionic liquids. An error of over 5 V renders the computed ECW practically useless for screening purposes. The HOMO-LUMO gap is known to significantly overestimate the electrochemical window because it neglects electrode interactions and kinetic limits, yet the paper relies on these computed values to filter candidates without correcting for this systematic bias.\n\"Electrochemical Windows of Room-Temperature Ionic Liquids from Molecular Dynamics and Density Functional Theory Calculations\" [2]\nThis reference (cited in the paper) and others in the field acknowledge that while HOMO-LUMO gaps provide a theoretical upper bound, they often fail to predict experimental stability limits accurately, necessitating more advanced methods or calibration, which are absent in this work.\n\nReferences:\n[2] Ong, S. P., Andreussi, O., Wu, Y., Marzari, N. & Ceder, G. Electrochemical Windows of Room-Temperature Ionic Liquids from Molecular Dynamics and Density Functional Theory Calculations. Chem. Mater. 23, 2979–2986 (2011). https://doi.org/10.1021/cm200679y", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "The claimed \"ensemble learning\" approach is not correctly implemented in the provided code, as the model saving mechanism overwrites the files for different algorithms, preventing the actual use of an ensemble for future predictions.\n\n```python\nclf_name = ['SVM', 'RF', 'XGB']\n...\nfor i in range(0, len(clf_name)):\n    ...\n    # save the model to disk\n    filename = self.abs_path + \"/scaler/\" + label_feature + '_xgb_model.sav'\n    pickle.dump(clf, open(filename, 'wb'))\n```\nThe code iterates through Support Vector Machine (SVM), Random Forest (RF), and XGBoost (XGB) classifiers but saves each trained model to the exact same filename (`_xgb_model.sav`). As a result, the SVM and RF models are overwritten, and only the final XGBoost model is preserved. This contradicts the paper's claim of using an ensemble method for the final recommendation and renders the `modelPrediction` function (which loads this single file) incapable of performing the described ensemble prediction.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "While the idea behind the simultaneous classification/prediction machine learning algorithm is brilliant, I am not convinced that this work will be of great significance for the field. The main reason for this is the absence of adequate validation of their predictions, which makes then their classification ambiguous. The authors are using a machine learning algorithm to predict the properties of interest in their system (here conductivity and electrochemical window), which however is at no point compared to literature data for the same compounds. I understand that since the studied dataset comes as a result of ion combinations, some of those ionic liquids are not commercially available, or maybe they have never been reported at all. But a comparison on a selected subset of ionic liquids is crucial.\\n\\nRegarding the experimental data, from a pool of 40 recommended ionic liquids the authors select 4 to use in their fuel cells. However, I believe that the selection of ionic liquids is not in agreement with the scope of the work. All 4 selected ionic liquids are commercially available and I believe that they were chosen so that the authors avoid synthesising their own compounds. The whole point of this work is to discover an optimised selection of ions for this application, but then the authors decide to work with 1-ethyl-3-methylimidazolium triflate and tetrafluoroborate, which are ‘old’ ionic liquids and they have been used since the 1990’s for electrochemical applications. I believe that as a proof of concept they should have tried at least one ‘unconventional’ combination of ions from their list. The results they obtain on their fuel cells are indeed very promising, but for an expert on the ionic liquid electrochemistry field it is not surprising or unexpected.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "As I mentioned in the previous section, there is no cross-reference for the prediction accuracy of the calculated properties. This should definitely be amended before publishing this article.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "During the ‘supervised learning’ section the authors introduce an additional filter to validate their data, by calculating the interaction energy between the anions and the cations. Figure 3c and Supplementary Table 1 show the results of these Energy calculations. To my opinion these calculations are problematic and they need revisiting. According to their formula, the energy values should be negative because the energy of the ion pair (E(+)[I-]) should be more negative than the individual energies of the ions. However, all the energies that are shown in Supplementary Table 1 are positive. The values of E(+)[I-], E+ and E- should also be shown in the ESI, for comparison reasons. Moreover, from my experience, the scale of those energies is unexpected, as I would expect the interaction energies in the range of minus a few hundreds kJ/mol. Depending on the geometry optimisation process the interaction energy can differ, so the graph shown in Figure 3c is expected to have an error bar of ±50 kJ/mol, which makes it impossible to extract certain results from it, as the two box plots mostly overlap. Before the article is considered for publication, the authors need to revisit their calculations, explain properly their calculation methodology and answer questions such as what convergence criteria they use, specify grid accuracy, did they check for absence of imaginary frequencies etc?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "Finally, something that is not so much of a flaw in the data analysis but more a part that needs further clarification is the part about the ion exchange with the ionic liquid electrolyte (rows 232-235). It is not clear to me why the incorporation of Li to the IPE is done with LiFSI and not with Li salt with the corresponding anion as the IPE (LiOTf and LiBF4 accordingly) and also why the ion exchange happens in [C3mpyr][FSI]? I assume that the authors have tried different solvents and have a reason for performing the ion exchange in another IL and not in a conventional volatile molecular solvent, but this should be clearly explained in the text.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "I am not convinced where the novelty and the importance of this work lies. There are many published articles on both ML algorithms for property prediction and conductive ionogels. I think that the authors need to add a paragraph (probably in the conclusions) highlighting the novelty of their work, what are the advantages of their algorithm compared to others and why their methodology/IPEs is superior to others reported in the literature.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "There are several grammatical/syntax errors throughout the text, language needs to be corrected.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "The company selling the ionic liquids is IoLiTec (in the text it is written as IoLiTech).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Human_1|9", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "The authors need to amend their abbreviations for their ionic liquids. For example 1-ethyl-3-methylimidazolium triflate, here it is abbreviated as C2mimTFO, the established abbreviation for that is either [Emim][OTf] or [C2C1im][OTf]. The authors need to correct their ILs abbreviations according to the literature.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Human_1|10", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "Figure 4. The embedded photos are too small for anyone to see them properly.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Human_1|11", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "Row 52. ‘Large population of ion pairs’ is wrong. It should be a large population of IL candidates", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Human_1|12", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "Row 52. Here they use the abbreviation ML but they define it later in text.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Human_1|13", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "Row 181. Geometric not gyometric.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Human_1|14", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "Row 232. If the authors claim that their films are mechanically strong, they need to perform a tensile stress analysis.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Human_1|15", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "Row 350. The Machine Learning methodology needs to be more detailed in order to be more reproducible.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Human_1|16", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "Row 360. The quantum chemistry calculations methodology needs more details to be reproducible.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Human_1|18", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "Rows 389. The thickness/diameters of the electrodes need to be stated.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "Very few details on the development of machine learning models are provided. I also find the development of the three machine models rather problematic as the data set is not split into a training and test data set making it difficult to assess the predictive capability of the model. This is especially concerning as it has been pointed out in the manuscript that the models tend to overfit due to over-representation of one or more cation/anion types.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "RDKit generates a large number of molecular descriptors for a given ionic liquid. Please include a description of how the total number of features was reduced to 60. Also specify if the cation and anion in an ionic liquid pair were modeled with different set of descriptors.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "Provide a reasoning for the basis set selection. Please include the level of theory for electronic structure calculations.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "Why was a particular threshold of ionic conductivity and ECW selected?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "It is confusing that output properties from models such as ionic conductivity and electrochemical windows are listed as features.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "It is not clear that spherical anions will yield liquids/solid from Figure 3a. In fact, there does not seem to be a correlation between the sphericity of the anions and phase.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "How were top 10 important features determined?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "The results on 20 ILs is not enough to establish the correlation. For 1000 ILs, it is not difficult to conduct quantum calculations. I would recommend at least 20% of the ILs on which these calculations are carried out ensuring that cation types and anions are well represented.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "Why is it necessary to choose hydrophilic ionic liquids for Li-ion batteries? In fact, this property will actually be detrimental to the performance of batteries if water is absorbed.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Human_2|10", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "Provide the rationale for using PBDT as a liquid crystalline polyelectrolyte.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|33|Human_2|11", "source": "prb", "split": "test", "paper_id": "prb33", "comment": "Provide a caption for Supplementary Table 2. Include units for ECW and ionic conductivity. Specify the temperature at which ionic conductivity is predicted. For many of the ionic liquids, measured ionic conductivities are available from the NIST ILThermo Database. A comparison must be made between predictions and the measurements.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|34|Claude|1", "source": "prb", "split": "test", "paper_id": "prb34", "comment": "The paper directly compares computationally predicted bulk conductivity from kinetic Monte Carlo (kMC) simulations with experimental total ionic conductivity measured from polycrystalline pellets, without adequately addressing that experimental measurements include grain boundary contributions that are not modeled in the simulations.\n\n\"our measured experimental conductivity (see Figure 4b) of ~ 0.1 S cm⁻¹ at 573 K is in excellent agreement with our computed value of ~ 0.2 S cm⁻¹\"\nThis comparison treats computational and experimental values as directly comparable despite fundamental methodological differences. The kMC simulations model only bulk (grain interior) diffusion in idealized perfect crystals, while the experimental impedance spectroscopy measurements on polycrystalline pellets include both bulk and grain boundary contributions. The supplementary materials reveal pellet compacities of only 69-77% (Table S6), indicating significant porosity and grain boundary density. Standard practice in the solid electrolyte field is to separate bulk and grain boundary contributions when comparing with computational results, as grain boundaries can significantly reduce measured conductivity, particularly in NASICON-type materials.\n\n* Quote from supplementary materials (Table S6): \"Compacity (%) x=1.5: 69.16; x=2.0: 71.21; x=2.4: 76.63\"\nThe low compacity values (less than 80%) indicate that the experimental pellets have significant porosity and grain boundary volume. In polycrystalline ceramics with such densification levels, the grain boundary contribution to total resistance can be substantial. The apparent \"agreement\" between computed (~0.2 S/cm) and experimental (~0.1 S/cm) values may be coincidental, as bulk conductivity in fully dense samples could be even higher than the experimental total conductivity, potentially indicating a larger discrepancy from computational predictions than suggested.\n\"The fitting of Nyquist plot was carried out using ZView software. For x = 1.5, the equivalent circuit used was based on semicircle phenomena... Applying the same equivalent circuit for other samples (x = 2.0 and x = 2.4) was not satisfactory, thus a one-phenomena Debye Model for solid electrolyte between two ionically blocking electrodes is used instead.\"\nThe use of different equivalent circuits for different compositions suggests that the impedance spectra could not be consistently analyzed to separate bulk and grain boundary contributions. The one-phenomena Debye model used for x = 2.0 and 2.4 compositions does not separate these contributions, yet the paper claims excellent agreement with bulk conductivity calculations. Ma et al. [[1]](#citation-1) demonstrated that for NASICON materials, bulk grain conductivity can exceed 0.01 S/cm at room temperature, significantly higher than total conductivity measured from typical polycrystalline samples.\n\nReferences:\n[1] Ma, Q. et al. Room temperature demonstration of a sodium superionic conductor with grain conductivity in excess of 0.01 S cm⁻¹ and its primary applications in symmetric battery cells. [*J. Mater. Chem. A* **7**, 7766–7776 (2019)](https://doi.org/10.1039/C9TA00048H)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|34|Claude|2", "source": "prb", "split": "test", "paper_id": "prb34", "comment": "The kinetic Monte Carlo simulations are exclusively based on the high-temperature rhombohedral (R3̄c) NASICON structure, yet experimental measurements at compositions x = 2.0 and x = 2.4 show clear monoclinic-to-rhombohedral phase transitions at ~433 K that significantly affect activation energies, creating a fundamental mismatch between simulation conditions and experimental reality.\n\n\"In the rhombohedral high-temperature NASICON structure (R3̄c), there are two independent and partially occupied sodium sites, Na(1) and Na(2).\"\nThe paper's theoretical framework and kMC model are explicitly built on the rhombohedral structure. This is appropriate for high-temperature simulations but not for comparing with experimental data measured across the phase transition. The monoclinic phase (C2/c) has different Na site orderings, local environments, and transport pathways that are not captured by the R3̄c-based model.\n\"Both compositions at x = 2.0 and x = 2.4 show two linear domains with different activation energies displayed in Figure 4b. Thus, the Arrhenius plots of Figure 4b reproduce the documented monoclinic-to-rhombohedral phase transition upon heating for the compositions Na₃Zr₂Si₂P₁O₁₂, and Na₃.₄Zr₂Si₂.₄P₀.₆O₁₂ at ~ 433 ± 15 K.\"\nThe experimental data clearly shows two distinct activation energy regimes (0.38 eV below and 0.22 eV above ~433 K) corresponding to the monoclinic and rhombohedral phases respectively. However, the kMC simulations were performed at 373, 473, and 573 K using only the R3̄c structure. At 373 K, the experimental samples are in the monoclinic phase with higher activation energy, but simulations model the rhombohedral phase. This fundamental inconsistency undermines direct comparisons between computed and measured conductivity at lower temperatures.\n\n* Quote from Figure 4a caption: \"In panel a, X-Ray diffraction pattern (dark blue, orange, and red circles), and Le Bail fitting (solid lines in cyan, dark brown and dark red) for synthesized Na₁₊ₓZr₂SiₓP₃₋ₓO₁₂ (x = 1.5, 2.0, and 2.4)\"\nThe XRD patterns confirm that at room temperature, compositions x = 2.0 and 2.4 adopt the monoclinic C2/c structure, not the rhombohedral R3̄c structure used in simulations. While phase transitions in NASICON are well-documented [[2]](#citation-2), the computational model does not account for the different ionic transport characteristics in the low-temperature monoclinic phase, which is structurally distinct and shows different Na migration pathways.\n\nReferences:\n[2] Jolley, A. G., Taylor, D. D., Schreiber, N. J. & Wachsman, E. D. Structural Investigation of Monoclinic-Rhombohedral Phase Transition in Na3Zr2Si2PO12 and Doped NASICON. [*J. Am. Ceram. Soc.* **98**, 2902–2907 (2015)](https://doi.org/10.1111/jace.13692)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|34|Claude|3", "source": "prb", "split": "test", "paper_id": "prb34", "comment": "The kinetic Monte Carlo simulations employ a fixed attempt frequency (ν = 0.5 × 10¹³ Hz) without justification, sensitivity analysis, or acknowledgment that this parameter directly affects the absolute values of predicted diffusivity and conductivity by orders of magnitude.\n\n* Quote from code (run_kmc.py, line 16): `v = 0.5*10**13`\nThe attempt frequency is hard-coded as a constant value of 5 THz across all compositions and temperatures. In transition state theory, the attempt frequency (also called the pre-exponential factor or vibrational prefactor) relates to phonon frequencies at the transition state and can vary significantly between different materials, compositions, and even different migration paths within the same material. The absolute diffusivity D and conductivity σ scale linearly with this parameter, meaning any error in the attempt frequency propagates directly to all predicted transport properties.\n\n* Quote from Methods section: \"We implemented a rejection-free kinetic Monte Carlo (kMC) simulation scheme in an in-house-code, as described in Refs.³⁹,⁴⁰\"\nWhile the paper references the theoretical framework for kMC, it does not discuss how the attempt frequency was determined or validated. The referenced works (Van der Ven et al. [[3]](#citation-3)) describe the methodology but the specific choice of 5 THz for NASICON is not justified. Studies on ionic conductors show that attempt frequencies can range from 10¹² to 10¹⁴ Hz depending on the system, and this variation alone could shift predicted conductivity by up to an order of magnitude. Without uncertainty quantification for this parameter, the reported \"excellent agreement\" with experiment cannot be rigorously evaluated.\n\"The grey band in panel b shows the interval of confidence of our predictions at 573 K, which is lower in magnitude than the variance of Na-ion conductivities observed experimentally\"\nWhile the paper presents confidence intervals for conductivity predictions, these reflect only the statistical variance from different Si/P configurations, not systematic uncertainties from model parameters like the attempt frequency. A proper uncertainty analysis would need to propagate errors from all assumed parameters. He et al. [[4]](#citation-4) established rigorous procedures for quantifying statistical variances in diffusion property calculations, emphasizing that absolute values are sensitive to multiple computational parameters beyond just configurational sampling.\n\nReferences:\n[3] Van der Ven, A., Ceder, G., Asta, M. & Tepesch, P. D. First-principles theory of ionic diffusion with nondilute carriers. [*Phys. Rev. B* **64**, 184307 (2001)](https://doi.org/10.1103/PhysRevB.64.184307)\n[4] He, X., Zhu, Y., Epstein, A. & Mo, Y. Statistical variances of diffusional properties from ab initio molecular dynamics simulations. [*npj Comput. Mater.* **4**, 18 (2018)](https://doi.org/10.1038/s41524-018-0074-y)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|34|Claude|4", "source": "prb", "split": "test", "paper_id": "prb34", "comment": "The paper performs extensive kMC simulations across 11 Na compositions spanning the full range of 0 ≤ x ≤ 3, but experimental validation is limited to only three compositions (x = 1.5, 2.0, 2.4), leaving the majority of the computational predictions, particularly at low Na content (x < 1.5) where conductivity is orders of magnitude lower, without experimental verification.\n\n\"In total, more than 2,000 kMC simulations were performed to predict the Na⁺ diffusivities and conductivities at selected temperatures of 373, 473 and 573 K of 50 NASICON models (with varying Si/P configurations) at 11 distinct Na concentrations.\"\nThe computational study systematically covers 11 compositions (x = 0.03, 0.3, 0.6, 0.9, 1.2, 1.5, 1.8, 2.1, 2.4, 2.7, 2.97), representing a significant investment in computational resources. However, this extensive compositional mapping is validated experimentally at only three points (x = 1.5, 2.0, 2.4), all in the high-conductivity regime. The predictions for low-Na compositions where conductivity is predicted to be 4-6 orders of magnitude lower remain entirely unvalidated.\n\"We have synthesized different compositions of the NASICON, namely, Na₂.₅Zr₂Si₁.₅P₁.₅O₁₂, Na₃Zr₂Si₂P₁O₁₂, and Na₃.₄Zr₂Si₂.₄P₀.₆O₁₂ and tested their Na-ion transport characteristics.\"\nThe three experimentally studied compositions all fall within the high-conductivity regime (x = 1.5 to 2.4). Key predictions about the sharp rise in conductivity from x = 0 to x ≈ 2 and the drop at x > 2.4 are not experimentally validated in this work. While low-conductivity compositions are more challenging to synthesize phase-pure and to measure accurately, the paper's strong conclusions about the composition-conductivity relationship across the full range would benefit from broader experimental validation. Prior literature exists for end-member compositions [[5]](#citation-5) but direct comparison under identical synthesis and measurement conditions is lacking.\n\"Our model also agrees with previous measurements¹⁸,¹⁹,³⁰,³² which report a low conductivity and diffusivity in Na₁Zr₂P₃O₁₂.\"\nFor the low-Na end-member, the paper relies on literature comparison rather than direct experimental validation in this study. Given the paper's emphasis on the large variability in reported conductivity values across different studies (\"Figure S6 reveals a significant spread of experimentally measured ionic conductivities from different reports\"), validating the full compositional range under controlled conditions would strengthen the conclusions about the optimal x ~ 2.4 composition.\n\nReferences:\n[5] Goodenough, J. B., Hong, H. Y.-P. & Kafalas, J. A. Fast Na⁺-ion transport in skeleton structures. [*Mater. Res. Bull.* **11**, 203–220 (1976)](https://doi.org/10.1016/0025-5408(76)90077-5)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|34|GPT|1", "source": "prb", "split": "test", "paper_id": "prb34", "comment": "This paper’s central “bridge the gap” claim is undermined because it compares kMC-predicted **bulk** conductivities against experimentally extracted **total** pellet conductivities without consistently separating bulk vs grain-boundary/contact contributions, weakening the validity of the reported quantitative agreement.\n\nFigure 2 | Computed Na-ion transport properties of Na_{1+x}Zr_2Si_xP_{3-x}O_{12} bulk based on kinetic Monte Carlo simulations.\nThis explicitly frames the simulated conductivities as **bulk** properties, i.e., an intrinsic crystal-level transport prediction. Bulk conductivity is not directly comparable to a pellet’s apparent conductivity unless microstructural contributions (grain boundaries, porosity, contacts) are removed or modeled. The paper later states it fits impedance data with different equivalent circuits across compositions, which can alter what component is being extracted. Without a clear, composition-consistent decomposition of bulk vs non-bulk impedance features, agreement may reflect compensating errors rather than a validated model. In solid electrolyte practice, reporting and comparing “bulk” and “total” conductivities requires careful impedance interpretation and often separate semicircle attribution. As written, the comparison risks overstating the strength of the theory–experiment reconciliation.\nAn example of a Nyquist plot used to extract the total ionic conductivity from the sintered pellets of the NASICON compositions at variable temperatures (373 K, 473 K, and 573 K) is given in Figure 4c.\nThis sentence states the experimental quantity being extracted is **total ionic conductivity** from sintered pellets, which generally includes multiple resistive contributions (bulk, grain boundary, contact) depending on microstructure and fitting model. Total pellet conductivity is known to be sensitive to density/porosity and grain-boundary chemistry, so it is not equivalent to single-crystal/bulk transport. The paper does not show a consistent procedure that isolates the bulk arc for every composition/temperature (and it even changes the circuit model across x), making the extracted “total” values non-uniform in meaning. Because the simulations intentionally omit grain boundaries and porosity, comparing them directly to total pellet values conflates fundamentally different transport regimes. This is especially consequential because the paper’s main narrative hinges on quantitative agreement “in line with our predictions.” The evidence therefore supports that the reported agreement is not methodologically well-grounded.\n<table>\n  <tr>\n    <th>x</th>\n    <th>Mass (g)</th>\n    <th>Thickness (cm)</th>\n    <th>Surface area (cm<sup>2</sup>)</th>\n    <th>Compacity (%)</th>\n  </tr>\n  <tr>\n    <td>1.5</td>\n    <td>0.16</td>\n    <td>0.23</td>\n    <td>0.31</td>\n    <td>69.16</td>\n  </tr>\n  <tr>\n    <td>2</td>\n    <td>0.16</td>\n    <td>0.23</td>\n    <td>0.30</td>\n    <td>71.21</td>\n  </tr>\n  <tr>\n    <td>2.4</td>\n    <td>0.15</td>\n    <td>0.20</td>\n    <td>0.29</td>\n    <td>76.63</td>\n  </tr>\n</table>\nThese reported pellet “Compacity (%)” values (≈69–77%) indicate the samples are not fully dense, implying significant porosity and potentially large tortuosity effects. In solid electrolytes, porosity and imperfect densification can reduce the measured macroscopic conductivity and distort impedance spectra (e.g., depressed semicircles, broadened distributions). This makes it even less defensible to treat the extracted pellet conductivity as a direct proxy for intrinsic bulk transport. Moreover, the compacity differs across compositions, creating a confounding variable precisely where the paper claims composition-driven transport optimization. Without a correction for porosity/density or a microstructure-controlled comparison (e.g., similar relative density across samples), the composition trend in “total conductivity” may partially reflect processing artifacts. As a result, the bridge between computed bulk and measured pellet transport is not demonstrated with the rigor needed for strong conclusions.\nNa3+xZr2Si2+xP1−xO12 was the very first series of NASICONs discovered some 40 years ago; however, separation of bulk conductivity from total conductivity at room temperature is still problematic.\nThis statement from an external NASICON conductivity study directly highlights that separating bulk from total conductivity is a recognized, nontrivial challenge in this material family ([1](https://pubs.rsc.org/en/content/articlelanding/2019/ta/c9ta00048h)). The reviewed paper’s own methodology explicitly uses “total ionic conductivity” from pellets, yet it uses the term “bulk” for its kMC outputs and treats agreement as validation. The external quote underscores that careful impedance deconvolution is required to make bulk-level statements from polycrystalline ceramics. By not presenting a consistent bulk/grain-boundary separation (or quantifying how circuit choice affects extracted values), the reviewed paper falls short of established caution in the literature. This matters because their claims extend beyond qualitative trends to numerical conductivities and “excellent agreement.” The discrepancy between best practice and the paper’s comparison approach supports the criticism as a major validity issue.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|34|GPT|2", "source": "prb", "split": "test", "paper_id": "prb34", "comment": "This paper’s temperature-dependent mechanistic conclusions for NASICON are not fully reliable because the kMC simulations freeze the host framework and appear to use a single lattice model, while the experiments explicitly exhibit a monoclinic-to-rhombohedral phase transition around 433 K that can change diffusion topology and barriers.\n\nIn the rhombohedral high-temperature NASICON structure (\\( R\\overline{3}c \\)), there are two independent and partially occupied sodium sites, Na(1) and Na(2).\nThis text sets the structural basis of the transport discussion in the **high-temperature rhombohedral** phase, which is appropriate above the known transition temperature. However, the paper also evaluates and compares transport at 373 K, which is below the reported transition for x = 2.0 and 2.4 compositions (and thus likely in the monoclinic regime). If the computational lattice model remains rhombohedral across all temperatures, then the predicted low-temperature conductivities and inferred mechanisms are structurally inconsistent with the experimental state. Such a mismatch can alter not only quantitative values but also qualitative site connectivity and bottleneck geometry. Because the paper attributes trends to local polyanion environments, any structural-symmetry change is a major confounder. Therefore, anchoring the model in the high-T structure while interpreting sub-transition data raises a significant validity concern.\nThus, the Arrhenius plots of Figure 4b reproduce the documented monoclinic-to-rhombohedral phase transition upon heating for the compositions Na<sub>3</sub>Zr<sub>2</sub>Si<sub>2</sub>P<sub>1</sub>O<sub>12</sub>, and Na<sub>3.4</sub>Zr<sub>2</sub>Si<sub>2.4</sub>P<sub>0.6</sub>O<sub>12</sub> at ~ 433 ± 15 K.\nThis sentence confirms the experiments traverse a crystallographic phase transition within the paper’s own temperature window (373–573 K). A structural phase transition commonly changes site energies, migration pathways, and potentially the dominant conduction bottlenecks, meaning transport parameters are not expected to be smoothly extrapolatable without explicitly modeling the correct phase. The paper uses this transition to interpret two Arrhenius domains and activation energies, which indicates that structure is central to the experimental interpretation. Yet the computational description provided does not show a corresponding phase-aware modeling strategy (e.g., separate kMC lattices/parameters for monoclinic vs rhombohedral). As a result, the claimed agreement across temperatures may be coincidental or limited to the high-T regime. This is a major issue because the paper’s conclusions and proposed optimization strategies are framed as temperature-general within the studied window.\nDuring the kMC simulation, only Na ions can hop while the remaining atoms are frozen.\nFreezing the framework is a strong modeling approximation: it removes lattice vibrations, local relaxations around migrating ions, and any coupling between polyanion configurations and framework distortions. While lattice kMC can be appropriate when the host is rigid and a single phase is assumed, this paper’s experimental section explicitly involves a phase transition and discusses temperature-dependent activation energies. In such cases, framework degrees of freedom and symmetry changes can be essential to transport, so a frozen-host approximation may miss key physics at least in one regime. Additionally, freezing all non-Na atoms implicitly assumes that the migration bottleneck geometry is temperature-invariant, which is generally less justified near transitions. The paper does not provide an analysis showing that this approximation remains valid across both monoclinic and rhombohedral regimes. Hence, this sentence directly supports the criticism that the mechanistic conclusions across temperature are not fully justified.\n```python\nprim_fname = '../inputs/prim.json'\n...\nevents_initialized = kmc.initialization(occ,prim_fname,fitting_results,fitting_results_site,events,supercell_shape,v,T)\n```\nThis code snippet indicates the kMC simulation is initialized from a single structural template file (`prim.json`) rather than switching lattice models by temperature/phase. If the primitive lattice is fixed, then the simulation’s site network and geometric constraints are fixed as well, which is inconsistent with a scenario where the experimental crystal symmetry changes near 433 K. In other words, the code operationalizes a single-lattice, frozen-framework diffusion model across the temperature range. That choice may still reproduce some averaged conductivities, but it limits mechanistic inference about how transport changes across phases. Because the paper argues for reconciling theory and experiment over a range of temperatures, the phase-insensitive model is a substantial methodological gap. The code therefore provides concrete evidence that the phase-transition physics is unlikely to be captured as modeled.\n```json\n\"title\" : \"NASICON_prim\",\n\"lattice_vectors\" : [\n  [4.593150 ,2.651856  , 7.393667],\n  [-4.593150, 2.651856 , 7.393667],\n  [-0.000000, -5.303713, 7.393667]\n]\n```\nThis JSON defines a single set of lattice vectors for the simulation lattice, reinforcing that the host geometry is fixed in the kMC runs. When a material undergoes a monoclinic-to-rhombohedral transition, the lattice parameters and symmetry relations change, which can alter diffusion channels and site connectivities. A fixed-lattice approach cannot represent such changes unless separate lattices are explicitly used and swapped by temperature. The paper does not describe such a two-lattice treatment, but instead reports simulations at 373, 473, and 573 K using the same kMC workflow. Therefore, the underlying structure used for transport at 373 K may not correspond to the experimentally present monoclinic phase for key compositions. This supports the criticism that the temperature-dependent conclusions are not fully validated.\nKMCLib - a general framework for lattice kinetic Monte Carlo (KMC) simulations\nThis external description emphasizes that “lattice kMC” frameworks are explicitly built around a fixed set of lattice sites and events ([4](https://raw.githubusercontent.com/leetmaa/KMCLib/master/README.md)). The reviewed paper likewise uses a lattice-event approach with predefined Na(1)↔Na(2) hops, which is consistent with standard lattice kMC practice. However, this also clarifies the limitation: such models do not naturally incorporate structural phase transitions unless the practitioner constructs separate lattices and event catalogs. Since the reviewed paper’s experimental behavior includes a documented phase transition within the modeled temperature range, the burden is on the authors to show phase-aware modeling or justify why a single lattice suffices. The lack of such justification makes the phase omission a significant threat to validity. The external quote thus supports the claim by situating the paper’s approach within a class of methods known to require special handling for phase changes.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|34|GPT|3", "source": "prb", "split": "test", "paper_id": "prb34", "comment": "The paper’s headline conductivity claims are potentially misleading because the abstract reports ~0.1 S cm^-1 for Na_{3.4}Zr_2Si_{2.4}P_{0.6}O_{12} without stating the temperature, while the main text indicates similarly large values only at elevated temperature (e.g., 573 K), weakening the robustness of the conclusions about “highest ionic conductivities” for practical solid-state battery conditions.\n\nWe performed impedance spectroscopy of samples with varying Na compositions revealing that the highest ionic conductivity (\\(~0.1\\ S\\ cm^{-1}\\)) is achieved in Na_{3.4}Zr_2Si_{2.4}P_{0.6}O_{12}, in line with our predictions (\\(~0.2\\ S\\ cm^{-1}\\)).\nThe abstract presents a very large conductivity value in S cm^-1 without specifying the temperature, which is critical because ionic conductivity in solids is strongly temperature dependent and commonly reported at a standard reference temperature (often ~25 °C) when discussing practical relevance. Without a temperature qualifier, a reader can reasonably interpret ~0.1 S cm^-1 as near-room-temperature performance, which would be extraordinary for oxide NaSICON ceramics. The main text later anchors comparable magnitudes at much higher temperatures, indicating that the abstract’s phrasing lacks essential context. Because the paper motivates the work partly by solid-state battery relevance, temperature ambiguity can materially distort the perceived significance. This is not a cosmetic issue: it affects whether the claimed performance is immediately actionable for typical operating conditions. Therefore, the omission undermines the clarity and can inflate the perceived impact.\nNonetheless, for Na\\(_3\\)Zr\\(_2\\)Si\\(_2\\)P\\(_1\\)O\\(_{12}\\) our measured experimental conductivity (see Figure 4b) of ~ 0.1 S cm\\(^{-1}\\) at 573 K is in excellent agreement with our computed value of ~ 0.2 S cm\\(^{-1}\\).\nThis sentence explicitly ties the ~0.1 S cm^-1 experimental value to **573 K**, which is far above room temperature. This directly shows that at least one of the headline-scale conductivities discussed in the paper occurs only at elevated temperature. When juxtaposed with the abstract’s temperature-free claim, it suggests the abstract compresses temperature-dependent performance into a single number without proper context. This matters because a conductivity of 0.1 S cm^-1 at 573 K does not imply similar performance at 298 K, given typical Arrhenius behavior and the paper’s own discussion of activation energies and phase transitions. As a result, the paper’s “highest ionic conductivity” statement is not robustly interpretable for practical conditions. The evidence supports that the narrative could overstate practical significance unless temperatures are made explicit.\nMeasurements were recorded every 50 K from 323 K to 623 K (15 minutes soaking each time), and then cooled down every 50 K from 623 K to 323 K.\nThis methods detail shows that the experimental impedance spectroscopy campaign is explicitly a **high-temperature** measurement protocol spanning 323–623 K. Given this, any claim of “highest ionic conductivity” should be reported together with the temperature (or as a room-temperature extrapolation with uncertainty), because the measured values are inherently temperature-indexed. The abstract does not clarify whether its 0.1 S cm^-1 refers to 373 K, 473 K, 573 K, or another temperature, even though the paper later emphasizes multiple Arrhenius regimes and a phase transition near 433 K. This ambiguity makes it hard to evaluate the claimed agreement between experiment and theory and to compare to the broader literature. In a field where room-temperature conductivity is often the benchmark for applicability, omitting temperature is a major interpretability flaw. The methods quote therefore supports that the headline performance statement is insufficiently grounded.\n... using a solution-assisted solid-state reaction for preparation of Na3+xZr2Si2+xP1−xO12, a total conductivity of 5 × 10−3 S cm−1 was achieved for Na3.4Zr2Si2.4P0.6O12 at 25 °C...\nThis external sentence provides a clear example of standard reporting practice: conductivity is explicitly stated **at 25 °C** and distinguished as “total conductivity” ([1](https://pubs.rsc.org/en/content/articlelanding/2019/ta/c9ta00048h)). It also gives a room-temperature benchmark for the same nominal composition family (including Na3.4Zr2Si2.4P0.6O12), reinforcing that temperature context substantially changes how large a reported conductivity is. The reviewed paper’s abstract does not provide an equivalent temperature qualifier, making its headline number hard to interpret relative to established room-temperature baselines. While different processing routes can yield different conductivities, the key issue here is that the external literature communicates temperature and measurement type explicitly. This contrast supports the criticism that the reviewed paper’s abstract overstates or at least obscures practical performance. The external quote therefore strengthens the case that the paper’s presentation could mislead readers about room-temperature applicability.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|34|GPT|4", "source": "prb", "split": "test", "paper_id": "prb34", "comment": "The paper’s conclusion that diffusivity/conductivity “cannot be used to identify” phase separation is not sufficiently supported because it asserts that a predicted ~1-order-of-magnitude signature is “within the error” without presenting quantified experimental uncertainties, statistical confidence intervals, or a sensitivity analysis showing detectability limits.\n\n... this dip in ion transport properties approximately accounts for one order of magnitude, well within the error of the available experiments and our calculations, thus making it challenging to detect the signature of phase separation via diffusivity/conductivity measurements or calculations.\nThis statement makes a strong detectability claim (“challenging to detect”) while only qualitatively referencing “the error” without quantifying it. In solid-state ionics, whether a one-order-of-magnitude change is detectable depends on the actual experimental uncertainty (including pellet-to-pellet variability, fitting ambiguity, and microstructure effects) and on the computational statistical uncertainty across sampled configurations. The paper does not provide error bars on the key transport plots nor a formal uncertainty propagation that would justify the detectability conclusion. Moreover, the computational model’s uncertainty is not transparently translated into confidence bounds on the phase-separation dip (e.g., distribution over configurations for the phase-separated ensembles). As a result, the inference that conductivity cannot identify phases is not robustly established. Because this conclusion is extended beyond NASICON (“may also be valid for other solid electrolytes and electrodes”), the lack of quantified uncertainty becomes a major issue.\nOur calculations suggest that Na diffusivity and conductivity cannot be used to identify the underlying phases within the NASICON electrolyte.\nThis is an unusually strong negative conclusion (“cannot be used”) that would normally require a careful power/detectability analysis demonstrating that, given realistic experimental noise and model uncertainty, transport signatures are statistically indistinguishable. The paper instead provides a qualitative argument and does not report, for example, the variance of conductivity across the phase-separated configurations relative to the solid-solution configurations. In practical terms, even if the average dip is ~10×, detectability could still be possible with controlled microstructure and repeated measurements—unless proven otherwise. The statement also risks conflating “difficult under typical measurement scatter” with “in principle impossible,” which are scientifically different. Without quantified uncertainties, the conclusion is not reliably supported by the presented evidence. This weakens the robustness of the paper’s broader guidance on identifying phase separation.\nThe grey band in panel b shows the interval of confidence of our predictions at 573 K, which is lower in magnitude than the variance of Na-ion conductivities observed experimentally (Figure S6).\nWhile this mentions an “interval of confidence,” the paper does not define how the confidence interval is computed (e.g., percentile range across 50 configurations, standard error of the mean, bootstrapping, or another method). Without a definition, it is unclear whether the grey band is a statistically meaningful uncertainty estimate that can be used to support detectability claims. Additionally, the phrase “variance ... observed experimentally” is not accompanied by experimental error bars or a measurement model explaining what portion of scatter is noise versus systematic differences across studies. For detectability of phase separation, the relevant comparison is not just “variance across literature reports,” but uncertainty under controlled conditions for the same processing and microstructure. Therefore, even where uncertainty language appears, it is insufficiently operationalized to justify the strong inference made. This supports the criticism that the statistical treatment is inadequate for the claimed conclusion.\n... the diffusional properties obtained from AIMD simulations are often plagued by poor statistics.\nThis external sentence highlights a general, well-known issue in computational ion-transport estimates: limited sampling can lead to unreliable diffusivities and conductivities unless statistics are carefully handled ([2](https://www.nature.com/articles/s41524-018-0074-y)). Although the reviewed paper uses kMC rather than AIMD and emphasizes large sampling, the same principle applies when making detectability claims based on differences that are only ~10×. To argue that a one-order-of-magnitude dip is “within error,” the authors need to clearly quantify statistical uncertainty in their kMC averages and compare it to experimental uncertainty under comparable conditions. The external quote underscores why simply asserting “within error” is inadequate: statistical reliability must be demonstrated, not assumed. This is especially important because the paper’s conclusion is negative and generalized beyond the specific system. Therefore, the external evidence supports the need for more rigorous uncertainty quantification than what is provided.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|34|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb34", "comment": "The paper claims that their Kinetic Monte Carlo (KMC) simulations predict the highest ionic conductivity at the composition $Na_{3.4}Zr_2Si_{2.4}P_{0.6}O_{12}$ ($x=2.4$). However, the provided KMC code and data predict a trend where conductivity increases as the silicon content decreases from $x=2.4$ to $x=1.8$, contradicting the paper's conclusion.\n\n\"Our predictions indicate that suitably doped NASICON compositions, especially with high silicon content, can achieve high Na^+ mobilities.\"\nThe paper emphasizes high silicon content ($x=2.4$) as the key to high mobility.\n\"highest ionic conductivity (~0.1 S cm^{-1}) is achieved in Na_{3.4}Zr_2Si_{2.4}P_{0.6}O_{12}, in line with our predictions (~0.2 S cm^{-1}).\"\nThis explicitly states that the prediction matches the experimental peak at $x=2.4$.\n```python\n# Results from running the provided KMC code at 573 K\n# comp=0.2 (x=2.4): Conductivity ~ 1.75 mS/cm\n# comp=0.3 (x=2.1): Conductivity ~ 6.84 mS/cm\n# comp=0.4 (x=1.8): Conductivity ~ 9.00 mS/cm\n```\nExecuting the provided `run_kmc.py` script with the provided `mc_results.h5` database reveals that the predicted conductivity at $x=1.8$ (~9.00 mS/cm) is more than five times higher than at $x=2.4$ (~1.75 mS/cm). This directly contradicts the claim that the model predicts a peak at $x=2.4$. The code predicts that lower silicon content (within this range) leads to higher conductivity.", "reviewer_type": "ai", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|34|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb34", "comment": "The paper claims that their KMC model predicts an ionic conductivity of approximately 0.2 S/cm (200 mS/cm) for the optimal composition. However, the provided code yields values around 0.002 S/cm (2 mS/cm) at the same temperature (573 K), which is two orders of magnitude lower.\n\n\"highest ionic conductivity (~0.1 S cm^{-1}) is achieved in Na_{3.4}Zr_2Si_{2.4}P_{0.6}O_{12}, in line with our predictions (~0.2 S cm^{-1}).\"\nThe authors claim a theoretical prediction of ~0.2 S/cm.\n```python\n# Output from run_kmc.py for x=2.4 at 573 K\n# Conductivity    1.753E+00\n```\nThe code output is in mS/cm (as confirmed by the unit conversion factor `1.602*10**11` in `kmc.py`). The value `1.753` corresponds to 1.753 mS/cm, or 0.001753 S/cm. This is approximately 100 times lower than the claimed 0.2 S/cm. This huge discrepancy suggests either a flaw in the model implementation provided, incorrect parameters (e.g., attempt frequency), or a misrepresentation of the theoretical results in the text.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|34|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb34", "comment": "The paper claims to achieve the \"highest ionic conductivity (~0.1 S cm^{-1})\" for NASICON. However, this value (likely at 300°C/573 K based on context) is not higher than values reported in early literature, such as 0.2 S/cm at 300°C reported by Hong in 1976.\n\n\"highest ionic conductivity (~0.1 S cm^{-1}) is achieved in Na_{3.4}Zr_2Si_{2.4}P_{0.6}O_{12}\"\nThe authors present 0.1 S/cm as a record-breaking value.\n\"The conductivity of Na_{3}Zr_{2}Si_{2}PO_{12} at 300°C is 0.2 (ohm-cm)^{-1}.\" [1]\nHong (1976) reported a conductivity of 0.2 S/cm at 300°C for the standard NASICON composition ($x=2$). The value reported in this manuscript (0.1 S/cm) is actually lower than this 40-year-old benchmark. Even if the authors refer to total conductivity vs. grain conductivity, the claim of \"highest ionic conductivity\" without qualification is misleading given the established literature values.\n\nReferences:\n[1] Hong, H. Y.-P. \"Crystal structures and crystal chemistry in the system Na_{1+x}Zr_2Si_xP_{3-x}O_{12}.\" Materials Research Bulletin 11, no. 2 (1976): 173-182. https://doi.org/10.1016/0025-5408(76)90073-8", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|34|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb34", "comment": "The abstract claims that the KMC simulations map the compositional space \"over an unprecedented time range – in the realm of milliseconds\". However, the provided code and parameters run for only 3000 KMC passes, which corresponds to a physical time scale of microseconds, not milliseconds.\n\n\"More than 2,000 distinct ab initio-based kinetic Monte Carlo simulations have been used to map the statistically vast compositional space of NASICON over an unprecedented time range – in the realm of milliseconds\"\nThe authors claim to reach millisecond time scales.\n```python\nkmc_pass = 3000\n# ...\n# Output from run_kmc.py\n# Pass    Time\n# 99      6.068E-08\n```\nIn the provided code, `kmc_pass` is set to 3000. The output shows that 100 passes correspond to approximately 60 nanoseconds ($6 \\times 10^{-8}$ s). Extrapolating linearly, 3000 passes would correspond to roughly 1.8 microseconds ($1.8 \\times 10^{-6}$ s). To reach 1 millisecond ($10^{-3}$ s), the simulation would need to run for over a billion passes, which is not reflected in the provided code configuration. The claim of \"milliseconds\" appears to be exaggerated by three orders of magnitude based on the provided evidence.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|34|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb34", "comment": "The measurement and analysis of the presented impedance results is not correct. It is unreasonable that for impedance measurements using ion-blocking electrodes the impedance spectra do not start at the origin (0,0) of the Nyquist impedance plot. The main example for this error is on Figure 4C, for the spectrum at 373 K, in which the blue semicircle extends from 25 Ohms to ca. 145 Ohms. Since the authors mention that they measured up to frequencies of 30 MHz, there is no reason for all the spectra to not start at the origin. A possible source for the offset is that the electrolyte is reacting with the gold contact materials. The formation of such Na-Au alloys is possible at the temperatures reported here, so the authors should check if the electrodes have been affected by the measurement conditions. The other explanation for the offset of the blue semicircle is that this corresponds to the grain boundary resistance of the sample. Since the samples tested are not dense (the authors report pellet densities in the range of 70-77%), it is likely that grain boundary resistances are the main contributor to the impedance spectra. If the explanation for the offset is the second one, then it is a big problem for the manuscript because the authors make direct comparisons of the theoretically obtained ionic conductivities and those obtained experimentally. Such a direct comparison is only possible with fully dense samples, impedance data single crystals or when the impedance data is analyzed considering grain (bulk) and grain boundary resistivities.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|34|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb34", "comment": "Since the impedance data analysis is flawed and it serves to support one of the key findings of the manuscript, namely “we have demonstrated that first principles- based kMC can access significantly longer time scales in the millisecond range and larger length scales (a total of 21,504 atom supercells in the present work), enabling us to approach experimental time and space resolutions and establish a robust link between measurements and theory”, I cannot recommend the manuscript for publication as is.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|34|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb34", "comment": "The authors should discuss the limitation of their method for long-range diffusion analyses since the method does not incorporate the effect of grain boundaries. This is of particular interest when trying to understand experimental results where the material’s microstructure can dominate the transport properties. Specifically in their work, where the authors compare their bulk (intra-grain) predicted transport properties with their experimental results, which seems to include both, bulk and grain boundaries (inter-grain) conductivity results. The authors could measure their transport properties at lower temperatures, which usually helps to decouple bulk and grain boundary resistances to Na+ transport. This would be highly important, given that the authors have employed different synthetic methodologies and obtained different relative densities, which impacts the total conductivity reported. SEM images should be included to compare if microstructures are still comparable.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|34|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb34", "comment": "The reported kMC method only allows for Na+ to move, constraining the rest of the atoms to fix positions. Considering that for other polyanion systems have been reported polyanion rotations during Na+ diffusion – so-called paddle-wheel effect, do the authors anticipate any limitation or their current methodology to this particular system or other sulphide systems where they expected to extend this methodology?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|34|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb34", "comment": "For the NBE method the authors have employed a temperature of 0 K, while with other methods and techniques temperatures above 300 K have been used. Do the authors expect a constant Arrehneious behaviour of the transport properties over the whole range of temperatures reported to make these results comparable?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|34|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb34", "comment": "This reviewer has some concerns regarding the temperature choices for their theoretical calculations. The authors use the structure obtained at 1500 K to mimic that of the maximum temperature employed during experimental synthesis. In most cases, however, materials are cooled down to ambient temperature naturally, allowing the crystal structure to relax. This also seems to be the case of their experimental condition – no quenching protocol is mentioned. The authors should discuss this point and recalculate it as necessary. Additionally, the authors must perform Rietveld refinements, rather than Le Bail fittings, to obtain full structural information, importantly Na distribution within Na(1) and Na(2) sites, stoichiometry as well as quantification of ZrO2 impurity presence. Particularly, the presence of this impurity is concerning in their Na = 3 sample, where a non-negligible amount or ZrO2 is detected, which could affect the total transport properties of the material. Additionally, the authors’ claim on phase purity of these compounds should be revised.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|34|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb34", "comment": "It would be helpful for the reader to include in the supporting information the structural parameters for the models employed. Considering these are quenched structures at 1500 K, which is the symmetry of their model used for the diffusion calculations? This is an important parameter considering the monoclinic to rhombohedral transition of the NASICON system at some compositions at temperatures below the quenching point selected. Additionally, Na+ occupancies across different sites could vary with temperature.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|34|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb34", "comment": "This reviewer also recommends the authors to calculate/show the windows sizes difference for Na+ diffusion when replacing P5+ with Si4+, and correlate these with their results/conclusions.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|34|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb34", "comment": "The authors should include in the abstract the temperature at which the reported conductivity is obtained. Furthermore, the authors claim high conductivity (page 28) of their sample with 0.1 mS cm-1 at 200 oC, considering the current state-of-the-art in the field this claim should be revised.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|34|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb34", "comment": "The authors should also consider including the effect of the higher or optimal Na stoichiometry when discussing the positive effect of P5+ substitution with Si4+ on page 26.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|34|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb34", "comment": "Structures with charge-neutral vacancies at initial and final images in the diffusion path were fully optimized until the interatomic forces were less than 0.01 eV/Å and stresses were less than 0.29 GPa. Stress tensor looks high, not zero. Normally it should be 0.05 GPa or less than this.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|35|Claude|1", "source": "prb", "split": "test", "paper_id": "prb35", "comment": "The paper introduces a \"utilization rate\" metric to measure the contribution of each scale in multi-scale learning, but the mathematical definition is flawed (the claimed range constraint is incorrect) and the methodology for obtaining single-scale models from multi-scale models is insufficiently described.\n\n\"For a multi-scale model \\(M\\), taking two scales \\(s_0\\) (atomic structure scale) and \\(s_1\\) (molecular network scale) as inputs, its utilization rates for \\(s_0\\) and \\(s_1\\) are defined as \\[ u(s_0|s) = \\frac{f(M) - f(M_1)}{f(M_1)}, \\]\"\nThis formula defines the utilization rate as (f(M) - f(M1))/f(M1). If the multi-scale model M significantly outperforms the single-scale model M1 (for instance, if f(M) = 0.95 and f(M1) = 0.5), then u(s0|s) = (0.95-0.5)/0.5 = 0.9, which is within [-1, 1]. However, if f(M1) is very small (approaching 0), the metric can grow unboundedly positive. The formula cannot guarantee that the utilization rate is \"constrained within the range of -1 to 1\" as claimed in the paper.\n\"It is constrained within the range of -1 to 1. A higher utilization rate indicates that the multi-scale model can benefit from incorporating this scale.\"\nThis claim is mathematically incorrect. The formula u(s0|s) = (f(M) - f(M1))/f(M1) can exceed 1 when f(M) > 2*f(M1), which is plausible in practice when the multi-scale model significantly outperforms a single-scale baseline. Conversely, the lower bound of -1 would only be reached if f(M) = 0. This discrepancy between the claimed properties and the actual mathematical definition undermines the validity of the utilization rate analysis presented in Section 2.4.\n\"Here, \\(M_0\\) and \\(M_1\\) represent single-scale models obtained from the multi-scale model \\(M\\), while \\(f\\) denotes the predicted evaluation function.\"\nThe methodology for \"obtaining\" single-scale models from the multi-scale model is not clearly specified. Are M0 and M1 the same models with one scale ablated (zeroed out)? Are they separately trained single-scale models? This ambiguity makes it impossible to reproduce the utilization rate analysis or verify whether the reported values (e.g., 0.009 for atomic structure scale in HIGH-PPI) are correct. Prior work on multimodal learning imbalance analysis, such as Wu et al. [[1]](#citation-1), typically uses gradient-based metrics which have clearer mathematical definitions.\n\nReferences:\n[1] Wu, N., Jastrzebski, S., Cho, K., Geras, K.J. \"Characterizing and overcoming the greedy nature of learning in multi-modal deep neural networks.\" International Conference on Machine Learning, pp. 24043–24055, 2022. [https://proceedings.mlr.press/v162/wu22d.html](https://proceedings.mlr.press/v162/wu22d.html)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|35|Claude|2", "source": "prb", "split": "test", "paper_id": "prb35", "comment": "The paper presents a formal variational EM framework with ELBO optimization in Equations 1-3, but the actual implementation resembles iterative pseudo-labeling rather than true variational inference, and this connection is not clearly established.\n\n\"Thus we instead optimize the evidence lower bound (ELBO) of the log-likelihood function: \\[ \\log p_\\theta(y_{\\mathcal{L}_V}|\\mathcal{G}, A) \\geq \\mathbb{E}_{q_\\phi(y_{\\mathcal{L}_U}|\\mathcal{G}, \\mathcal{D})}[\\log p_\\theta(y_{\\mathcal{L}_V}, y_{\\mathcal{L}_U}|\\mathcal{G}, A)] - \\mathrm{KL}(q_\\phi(y_{\\mathcal{L}_U}|\\mathcal{G}, \\mathcal{D})||p_\\theta(y_{\\mathcal{L}_U}|\\mathcal{G}, A)) \\]\"\nThe paper frames the problem as ELBO maximization, which is the standard variational inference objective. However, the actual implementation in the code shows that the method generates pseudo-labels using hard thresholding (predictions > 0.7) and adds pseudo-edges to the network, which is fundamentally different from optimizing a variational distribution q_phi. True variational EM would involve maintaining probability distributions over unobserved variables and computing expectations, not hard pseudo-label assignments.\n\n* Quote from the code (trainer_ppi.py, line 631):\n```python\npseudo_labels.append((pseudo_preds.sigmoid() > 0.7).type(torch.FloatTensor))\n```\nThis hard thresholding at 0.7 to generate pseudo-labels is a self-training/pseudo-labeling approach, not variational inference. In variational EM, the E-step involves computing posterior expectations E_q[y], not hard binary assignments. The disconnect between the mathematical formulation (continuous probability distributions, KL divergences) and the implementation (hard thresholding) raises questions about whether the theoretical guarantees of variational EM actually apply to this method.\n\"We followed the idea of [18, 21] to utilize the wake-sleep algorithm [43] for minimizing the reverse KL divergence\"\nWhile the paper cites the wake-sleep algorithm, the actual implementation does not follow the standard wake-sleep procedure. The original wake-sleep algorithm [[2]](#citation-2) involves two distinct phases: a wake phase for training generative weights using recognition-generated samples, and a sleep phase for training recognition weights using generatively-sampled data. The pseudo-label mechanism in MUSE is structurally different, as it uses one model's hard predictions to augment training data for another model, rather than matching the wake-sleep framework's mutual information maximization objective.\n\nReferences:\n[2] Hinton, G.E., Dayan, P., Frey, B.J., Neal, R.M. \"The wake-sleep algorithm for unsupervised neural networks.\" Science, 268(5214), 1158–1161, 1995. [https://www.science.org/doi/10.1126/science.7761831](https://www.science.org/doi/10.1126/science.7761831)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|35|Claude|3", "source": "prb", "split": "test", "paper_id": "prb35", "comment": "Figure 5c shows that the optimal pseudo-label threshold is around t=0.4, but the implementation uses a fixed threshold of 0.7, which contradicts the ablation study findings.\n\n* Quote from Figure 5 caption: \"The molecular network scale performance (Best-F1) of MUSE with the different threshold of pseudo labels from the atomic structure model indicates that the mutual supervision in MUSE leads to superior performance.\"\nAccording to Figure 5c, the Best-F1 score peaks at threshold t=0.4 (approximately 0.953) and then decreases for higher thresholds. At t=0.5, the performance drops to approximately 0.933. This suggests that using a threshold of 0.4 would yield the best results according to the authors' own ablation study.\n\n* Quote from the code (trainer_ppi.py, line 631):\n```python\npseudo_labels.append((pseudo_preds.sigmoid() > 0.7).type(torch.FloatTensor))\n```\nThe hardcoded threshold of 0.7 in the implementation directly contradicts the ablation study findings. If the ablation study was conducted properly and shows optimal performance at t=0.4, the main experiments should use t=0.4, not t=0.7. This discrepancy raises concerns about whether the reported results in the paper were obtained using different hyperparameters than those in the released code, which would affect reproducibility.\n\n* Quote from paper: \"Subsequently, the performance gradually decreases as the threshold \\( t \\) increases, indicating that the predicted pseudo interactions become increasingly noisy when \\( t > 0.4 \\).\"\nThe paper explicitly states that performance degrades for t > 0.4 due to noisy pseudo-labels. However, the released implementation uses t=0.7, which according to the paper's own analysis would include more noisy pseudo-labels. This inconsistency between the paper's conclusions about hyperparameter sensitivity and the actual implementation code undermines the reproducibility and validity of the reported results.", "reviewer_type": "ai", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|35|Claude|4", "source": "prb", "split": "test", "paper_id": "prb35", "comment": "The bar plots in Figure 2c present performance comparisons without error bars or statistical significance tests, despite the supplementary materials showing that experiments were repeated 5 times with non-trivial variance.\n\n* Quote from the supplementary: \"Experiments were conducted 5 times, and the mean and standard deviation of AUROC and AUPRC are reported in Table S2.\"\nThe supplementary materials confirm that experiments were conducted with 5 repetitions and standard deviations were computed. However, Figure 2c in the main paper shows bar plots comparing methods across different splits (Random, BFS, DFS) without displaying any error bars. This omission makes it difficult to assess whether the reported improvements are statistically significant or within the margin of experimental variation.\n\n* Quote from supplementary Table S2 (partial): \"0.971 ± 0.003 | 0.952 ± 0.004 | 0.888 ± 0.004 | 0.754 ± 0.002 | 0.895 ± 0.001 | 0.723 ± 0.003\"\nThe supplementary tables show standard deviations of 0.003-0.004 for metrics like AUROC and Best-F1. These are non-trivial variances that should be displayed in the main figures. For instance, the claimed improvement over HIGH-PPI of \"8.41% in the BFS split\" should be accompanied by statistical tests to confirm significance. Without error bars, readers cannot determine if the observed differences exceed the experimental noise.\n\n* Quote from paper: \"Our model showed substantial improvements over the strongest baseline HIGH-PPI, which also incorporates multi-scale information for enhanced predictions, with an increase of 8.41% in the BFS split, 13.04% in the DFS split, 7.69% in the Random split\"\nClaims of \"substantial improvements\" should be supported by statistical significance tests, particularly when comparing to strong baselines. Standard practice in machine learning research, as recommended in reporting guidelines [[3]](#citation-3), calls for presenting confidence intervals or conducting significance tests when making comparative claims. The absence of such analysis weakens the strength of the conclusions.\n\nReferences:\n[3] Bouthillier, X., et al. \"Accounting for variance in machine learning benchmarks.\" Proceedings of Machine Learning and Systems, 3, 747-769, 2021. [https://proceedings.mlsys.org/paper_files/paper/2021/hash/cfecdb276f634854f3ef915e2e980c31-Abstract.html](https://proceedings.mlsys.org/paper_files/paper/2021/hash/cfecdb276f634854f3ef915e2e980c31-Abstract.html)", "reviewer_type": "ai", "label": "error", "error_type": "Neglect", "label_origin": "expert+llm-filter"}
{"id": "prb|35|Claude|5", "source": "prb", "split": "test", "paper_id": "prb35", "comment": "Supplementary Table S2 contains a suspicious entry \"0.922 ± 0.08\" for MUSE's AUPRC on DDI, which has an inconsistent number of significant digits and an anomalously high standard deviation compared to other entries.\n\n* Quote from supplementary Table S2: \"MUSE: 0.915 ± 0.005 | 0.922 ± 0.08 | 0.888 ± 0.003 | 0.791 ± 0.003 | 0.895 ± 0.005 | 0.846 ± 0.006\"\nThe entry \"0.922 ± 0.08\" stands out for two reasons: (1) it uses only one decimal place for the standard deviation while all other entries use three decimal places (e.g., 0.005, 0.003), and (2) the standard deviation 0.08 is approximately 16x larger than the typical standard deviations reported elsewhere in the table (ranging from 0.001 to 0.015). This suggests a potential typo where \"0.08\" should likely be \"0.008\".\n\n* Quote from supplementary: \"Experiments were conducted 5 times, and the mean and standard deviation of AUROC and AUPRC are reported in Table S3.\"\nIf the reported standard deviation of 0.08 for AUPRC is correct (not a typo), this would indicate unusually high variance for MUSE on the DDI task compared to all other metrics and methods. Such high variance would be inconsistent with the claim that MUSE provides stable and reliable predictions. This inconsistency warrants clarification, as it either represents a data quality issue or a reporting error that affects the interpretation of the DDI results.\n\n* Quote from the preceding row in Table S2 for MUSE-Joint: \"0.897 ± 0.011 | 0.910 ± 0.014\"\nThe MUSE-Joint ablation, which uses similar architecture, shows standard deviations of 0.011 and 0.014 for the same metrics. If MUSE truly had a standard deviation of 0.08 (nearly 6x higher), this would suggest significant instability in the proposed method compared to its simpler variant, which contradicts the paper's narrative about MUSE providing more balanced and stable multi-scale learning.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|35|GPT|1", "source": "prb", "split": "test", "paper_id": "prb35", "comment": "This paper’s reported SHS27K protein–protein interaction (PPI) gains are not a valid estimate of generalization because the PPI evaluation lacks a validation split and the released code uses the test split for model selection/early stopping and for pseudo-edge augmentation, directly undermining the paper’s state-of-the-art performance claims.\n\n\"Specifically, on the PPI dataset, MUSE outperformed all existing models including single-scale (DrugVQA [8] and TAG-PPI [25]), and multi-view methods (GNN-PPI [22] and HIGH-PPI [15]). TAG-PPI and DrugVQA, which solely focus on the atomic structure scale, achieved the poorest performance as they neglected the molecular network scale information. Our model showed substantial improvements over the strongest baseline HIGH-PPI, which also incorporates multi-scale information for enhanced predictions, with an increase of 8.41% in the BFS split, 13.04% in the DFS split, 7.69% in the Random split, (Fig. 2c and Fig. S1).\"\nThis passage is the paper’s central empirical claim for multi-scale interaction prediction on SHS27K, asserting large improvements over the strongest baseline across three splits. Such claims require a strictly held-out test set so that the reported numbers reflect generalization rather than adaptation to the evaluation labels. Because the magnitude of the claimed gains (e.g., 13.04% on DFS) is used to justify the overall superiority of the EM framework, any test-set contamination directly affects the paper’s conclusions. In common ML practice, test labels must not influence checkpoint selection, early stopping, threshold tuning, or graph augmentation decisions. Therefore, if the experimental protocol does not isolate the test set, this specific performance claim becomes unreliable as evidence of a better method.\n\"<td>Random</td>\\n    <td>5328</td>\\n    <td>-</td>\\n    <td>1332</td>\"\nThis row from Table S1 shows that, for SHS27K under the Random split, the Validation column is explicitly marked as \"-\", i.e., no validation set is used. Without a validation split, the usual mechanisms for selecting hyperparameters, choosing the best epoch, and early stopping cannot be performed without touching the test set. In graph learning papers, it is standard to reserve validation data for model selection precisely to avoid optimistic bias in the final reported test numbers. The absence of validation is especially problematic here because the method is iterative (multi-iteration EM), which increases the number of opportunities to inadvertently tune toward the evaluation set. Thus, the table itself signals a high risk that the test set may be used as a surrogate validation set.\n```python\nclass PPILinkTrainer:\n    def create_dataloaders(self):\n        split_edges = self.dataset.get_edge_split()\n        return split_edges['train'], split_edges['test']\n\n    def train(self, gnn_model=None, protein_dataset=None, protein_embeddings=None, em_iter=0):\n        ...\n        for self.cur_epoch in range(self.run_config.link_epochs):\n            ...\n            valid_loss, test_metrics = self.evaluate(self.graph, self.test_edges, self.test_label)\n            ...\n            if best_valid_f1 < test_metrics.F1:\n                best_valid_f1 = test_metrics.F1\n                ...\n                torch.save({...}, os.path.join(self.args.res_dir, f'link_{em_iter}_best_model.ckpt'))\n            ...\n            if stopper > self.patience:\n                write_log(self.logging, \"Early Stopping.\")\n                break\n```\nThis code makes the test split (\"split_edges['test']\") the only non-training split used inside training, and then evaluates on it every epoch to choose the best checkpoint (via best_valid_f1). That means test labels directly control early stopping and model selection, which invalidates the test set as an unbiased estimator of generalization. The problem is not merely a naming issue: the model is explicitly saved based on the best score computed on the held-out split it later reports as \"Validation_avg\" in logs. This creates systematic optimistic bias because the training loop can select epochs that happen to perform well on that same evaluation set. In standard benchmarking, the test set should be evaluated once after all training decisions are fixed using only training/validation data. Consequently, the reported SHS27K performance can be inflated by construction.\n```python\nif gnn_model is not None:\n    pseudo_edges = self.gnn_inference(gnn_model, protein_dataset)\n    self.graph.edge_index = torch.cat([self.graph.edge_index, pseudo_edges.to(self.device)], dim=1)\n\n...\n\ndef gnn_inference(self, gnn_model, protein_dataset):\n    ...\n    num_batches = int(len(self.test_edges) // batch_size)\n    for batch_index in range(num_batches):\n        edges = self.test_edges[batch_index*batch_size : (batch_index+1)*batch_size]\n        ...\n    ...\n    pseudo_edges = self.test_edges[pseudo_edges_idx].squeeze(1).t()\n    ...\n    return pseudo_edges\n```\nHere the model explicitly constructs pseudo edges from self.test_edges and injects them into the training graph via concatenation to self.graph.edge_index. Even if the pseudo labels are predicted (rather than ground-truth), this is still a form of transductive adaptation to the evaluation set because the held-out edges are being added into the graph used for message passing and subsequent optimization. Since the same test_edges are later evaluated for performance, the procedure risks a circular evaluation in which the model is trained on (or structurally conditioned on) the very edges it is asked to predict. This is materially different from using only the training graph plus unlabeled nodes, as it directly exposes the model to the test edge list during training. Such leakage is especially consequential in link prediction, where the graph structure is itself the primary signal. As a result, the evaluation no longer cleanly measures predictive performance on unseen interactions.\n\"Such experimental setup favors the model that overfits the most and defeats the main purpose of using a train/validation/test split — finding the model with the best generalization properties [Friedman et al., 2001].\" [[2]](#ref2)\nThis statement from the graph ML evaluation literature explains why the train/validation/test separation exists: to select models based on validation performance while preserving a clean estimate of generalization on the test set. The paper under review effectively collapses validation into test for SHS27K (as evidenced by Table S1 and the training code), which is exactly the kind of setup criticized here. The issue is not cosmetic; it changes which model is selected and can change the apparent ranking of methods. This matters particularly for iterative training paradigms (like EM-style alternation) where repeated evaluation increases the chance of selecting a checkpoint that performs well on the test split by chance. The quoted guidance reflects a widely accepted standard for fair comparisons across architectures and training procedures. Therefore, by violating this principle, the paper’s SHS27K PPI claims do not meet common validity expectations.\n\"Failure to identify the sources of empirical gains, e.g. emphasizing unnecessary modifications to neural architectures when gains actually stem from hyper-parameter tuning.\" [[5]](#ref5)\nThis observation is relevant because the paper attributes improvements to its EM-based multi-scale training paradigm and mutual supervision, but the code reveals additional evaluation-coupled choices (e.g., selecting checkpoints by test performance and augmenting with test edges). When evaluation leakage exists, it becomes impossible to disentangle whether reported gains come from the proposed methodological contribution or from training/evaluation artifacts. In other words, the experimental setup itself can become a confounder that produces performance gains unrelated to the core algorithmic idea. In fields like graph link prediction, subtle changes to data splits and selection criteria are known to materially change results, so rigor in isolating sources of gains is essential. The quoted critique highlights why ablation and proper selection protocols are required to support causal claims about what made performance improve. Thus, the paper’s attribution of gains to the EM framework is not well-supported under the observed evaluation procedure.\n\nReferences:\n[2] <a id=\"ref2\"></a>[Oleksandr Shchur et al., \"Pitfalls of Graph Neural Network Evaluation\" (NeurIPS 2018 Workshop).](https://arxiv.org/abs/1811.05868)\n[5] <a id=\"ref5\"></a>[Zachary C. Lipton and Jacob Steinhardt, \"Troubling Trends in Machine Learning Scholarship\" (2018).](https://arxiv.org/abs/1807.03341)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|35|GPT|2", "source": "prb", "split": "test", "paper_id": "prb35", "comment": "This paper’s drug–protein interaction (DPI) conclusions on BioSNAP are not robust because the dataset construction assumes randomly sampled “negative” drug–protein pairs from unobserved interactions, which can introduce false negatives and systematically inflate reported metrics, especially given the near-saturated AUPRC/AUROC values emphasized as state-of-the-art.\n\n\"The BioSNAP dataset, obtained from [23], consists of only positive drug-target interactions. The negative drug-protein interactions were generated by randomly selecting an equal number of protein–drug pairs [14, 26].\"\nThis sentence states that the benchmark’s negative class is not experimentally verified but is synthetically created by random sampling from unobserved pairs. In drug–target interaction data, “unobserved” does not imply “non-interacting,” so this procedure can label unknown positives as negatives, introducing false negatives and noise into both training and evaluation. Moreover, sampling an equal number of negatives enforces an artificial class balance that may not reflect real-world prevalence and can make the classification problem easier than practical deployment scenarios. Because the paper’s claims depend on very high AUPRC/AUROC, even small amounts of label noise or overly easy negatives can substantially change apparent performance. Common practice in DTI/DTI-like benchmarks is to test generalization under more realistic splits (e.g., unseen proteins/drugs) and/or harder, biologically plausible negatives to avoid inflated scores. Therefore, the stated negative sampling strategy weakens the credibility of the DPI performance claims.\n\"MUSE achieved the AUPRC of 0.998 and 0.922 and the AUROC of 0.993 and 0.915 respectively on the DDI and DPI datasets (Supplementary Table S2-S3).\"\nReporting an AUPRC of 0.998 and AUROC of 0.993 for DPI suggests the task is nearly solved under the chosen benchmark setup, which raises concerns about whether the evaluation is capturing real generalization difficulty. In imbalanced biological interaction prediction, near-perfect PR/ROC performance often indicates that the negative set is too easy, too small, or contains biases that can be exploited by the model. Because the negative class is constructed via random sampling from unobserved pairs, the evaluation may reward dataset-specific artifacts (e.g., degree effects, popularity biases, or trivial separability) rather than genuine mechanistic recognition. The paper uses these metrics to argue broad superiority of the multi-scale EM framework, but such near-saturation makes it hard to assess whether improvements are meaningful in practice. Stronger evidence would require demonstrating robustness under more challenging negative sampling and reporting how performance changes when negatives are curated differently. Without that, the conclusions drawn from these headline DPI metrics are not reliable.\n\"This is a drug-target interaction network that contains information on which genes (i.e., proteins encoded by genes) are targeted by drugs that are on the U.S. market.\" [[3]](#ref3)\nThis BioSNAP dataset description emphasizes that the resource records known drug–target relationships, i.e., observed positives, rather than experimentally confirmed negatives. This matches the paper’s statement that BioSNAP provides only positive interactions and reinforces that the negative class must be imposed by an external assumption rather than sourced from the dataset itself. When negatives are not curated, different negative sampling choices can lead to materially different benchmark difficulty and model rankings, making cross-paper comparisons fragile. In addition, since the dataset is based on drugs “on the U.S. market,” there can be strong confounders (e.g., well-studied drugs and targets) that correlate with interaction presence and can be amplified by random negative sampling. Therefore, treating randomly sampled unobserved pairs as ground-truth negatives is a methodological choice that substantially shapes the DPI task definition. This supports the criticism that the reported DPI results may not generalize beyond this particular synthetic labeling scheme.\n\"Simple random sampling of unobserved pairs for negative labels introduces significant noise and bias from potential false negatives.\" [[4]](#ref4)\nThis statement from recent DTI benchmarking work directly articulates the key methodological risk present in the paper under review: random negatives from unobserved pairs can be wrong (false negatives) and biased. The consequence is that both training and evaluation metrics may become unreliable indicators of real predictive utility, because models may be rewarded for exploiting biases rather than identifying true biochemical compatibility. This is especially relevant when reported metrics approach saturation, because noise and bias can dominate the apparent difficulty of the benchmark. The quoted source also indicates that addressing this requires more informed negative sampling strategies, which the paper under review does not describe beyond random selection. Hence, external literature supports the critique that the paper’s DPI protocol is prone to optimistic evaluation. This undermines the strength of the paper’s conclusions about state-of-the-art DPI performance.\n\"In addition, many studies follow the convention of using random splits to generate training/test sets (Kipf & Welling, 2017; Xu et al., 2019; Bordes et al., 2013), which is not realistic or useful for real-world applications and generally leads to overly optimistic performance results (Lohr, 2009).\" [[1]](#ref1)\nThis benchmark paper highlights a general evaluation pitfall: conventional random splitting practices often produce overly optimistic results that do not reflect real-world deployment. While the paper under review includes “Unseen Protein” and “Unseen Drugs” variants in the supplementary, its negative construction is still based on random sampling from unobserved pairs, which can similarly create optimistic evaluation conditions. The core point is that benchmark design choices (splits and negative sampling) can make results look substantially better than they would under realistic distribution shifts. For interaction prediction tasks, this matters because practical use often involves predicting interactions for novel targets or compounds and under substantial selection bias in what has been experimentally measured. The quote provides field-level context that evaluation protocols should be “meaningful” and avoid optimistic artifacts. Therefore, it supports the criticism that the paper’s DPI conclusions may not be robust to more realistic benchmarking protocols.\n\nReferences:\n[1] <a id=\"ref1\"></a>[Weihua Hu et al., \"Open Graph Benchmark: Datasets for Machine Learning on Graphs\" (NeurIPS 2020).](https://arxiv.org/abs/2005.00687)\n[3] <a id=\"ref3\"></a>[Stanford SNAP BioSNAP: \"Drug-target interaction network\" (ChG-Miner dataset page).](http://snap.stanford.edu/biodata/datasets/10002/10002-ChG-Miner.html)\n[4] <a id=\"ref4\"></a>[Yang Zhang et al., \"The structure-preserving spectral graph neural network for dual kinase inhibitors and synergy scoring in gastric cancer\" (npj Digital Medicine, 2026).](https://www.nature.com/articles/s41746-025-02240-7)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|35|GPT|3", "source": "prb", "split": "test", "paper_id": "prb35", "comment": "The paper’s reproducibility is substantially undermined because the released codebase contradicts its own installation claims by (i) failing on non-GPU machines at import time, (ii) hard-requiring multiple NVIDIA GPUs in training scripts, and (iii) using hard-coded, non-portable absolute paths for critical split files.\n\n\"We provide a script (install.sh) to install the environment, including the extra packages (mol2vec, descriptastorus, et al), and CPU and CUDA11.8 environments are supported.\"\nThis statement promises that the provided implementation can run in CPU-only environments, which is an important reproducibility commitment for researchers without access to NVIDIA GPUs. In computational biology, many users rely on CPU clusters or limited GPU resources, so CPU support materially affects who can reproduce the results. Because the claim is explicit (“CPU and CUDA11.8 environments are supported”), readers are entitled to expect that importing and running the code will not hard-fail when CUDA is unavailable. If the codebase contradicts this promise, the experimental results cannot be independently verified by a substantial fraction of the community. This is not a minor documentation mismatch: it directly affects whether the methods and results are reproducible at all. Therefore, the paper’s methodological transparency is weakened by this inconsistency.\n```python\nif check_gpus():\n    ...\nelse:\n    raise ImportError('GPU available check failed')\n```\nThis code path raises an ImportError during module import whenever torch.cuda.is_available() is false (or nvidia-smi is absent), which directly contradicts the stated CPU support. Because utils.py is imported by the training scripts, this behavior prevents even CPU-only preprocessing or partial runs, blocking reproduction in environments without NVIDIA tooling. The failure occurs before any model-specific code executes, so users cannot easily bypass it without modifying the source. In reproducible research code, GPU acceleration may be optional, but GPU absence should not cause unconditional import-time crashes; instead, it is usually handled by device selection logic. As written, the code enforces a stronger constraint than the paper/README describes. This mismatch is a major barrier to independent verification.\n```python\nself.device, self.device2 = GPUManager().auto_choice(num=2)\n```\nThis line requires the GPUManager to allocate two GPU devices, implying that the default training configuration depends on having at least two NVIDIA GPUs available. Many academic and industry environments (including cloud instances) provide only a single GPU per job, so this requirement can prevent straightforward reproduction of the training procedure even for GPU users. The paper does not clearly justify why two GPUs are necessary (as opposed to optional) for the reported experiments, nor does it provide a documented single-GPU fallback. When code implicitly assumes multi-GPU availability, reported compute cost and accessibility become unclear, and reproducing results becomes substantially harder. This is particularly problematic given that the method is iterative (multiple EM iterations), which already increases computational burden. Thus, the training script’s device assumptions undermine reproducibility.\n```python\nsplits = json.load(open(\"/data/user/raojh/worksapce/MUSE/data/high_ppi/split/random/train_val_split_1.json\", \"r\"))\n```\nThis hard-coded absolute path points to a user-specific filesystem location and is not portable across machines, operating systems, or repository checkouts. Because this file is used to construct splits (“train_index” and “valid_index”), it directly affects what data is used for training and evaluation, making it a critical part of experimental reproducibility. If the split definition depends on an external path that is not bundled and not parameterized, third parties cannot reliably reproduce the reported splits, even if they have the raw dataset. In benchmarked link prediction tasks, split definitions are often the single largest driver of performance variation, so this is not a minor engineering detail. The presence of such hard-coded paths indicates the codebase may reflect an internal environment rather than a fully packaged reproducible artifact. Therefore, the code as provided does not meet common reproducibility expectations for computational methods papers.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|35|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb35", "comment": "The paper's methodology contains a severe data leakage issue where predicted interactions from the test set are added to the molecular network graph, which is then used to predict the existence of those same interactions.\n\n```python\n# In trainer_ppi.py\ndef gnn_inference(self, gnn_model, protein_dataset):\n    # ...\n    # Uses test_edges to generate predictions\n    edges = self.test_edges[batch_index*batch_size : (batch_index+1)*batch_size]\n    # ...\n    pseudo_preds = gnn_model(batch)\n    pseudo_labels.append((pseudo_preds.sigmoid() > 0.7).type(torch.FloatTensor))\n    # ...\n    # Returns edges that are in the test set\n    return pseudo_edges \n\ndef train(self, gnn_model=None, protein_dataset=None, protein_embeddings=None, em_iter=0):\n    # ...\n    if gnn_model is not None:\n        # Adds predicted test edges to the graph\n        pseudo_edges = self.gnn_inference(gnn_model, protein_dataset)\n        self.graph.edge_index = torch.cat([self.graph.edge_index, pseudo_edges.to(self.device)], dim=1)\n    # ...\n    # Evaluates on the same test edges using the augmented graph\n    valid_loss, test_metrics = self.evaluate(self.graph, self.test_edges, self.test_label)\n```\nThe code explicitly uses the `test_edges` to generate pseudo-labels using the atomic structure model (`gnn_inference`). These edges, if predicted with high confidence, are then added to `self.graph.edge_index`. Subsequently, the molecular network model is evaluated on the same `test_edges` using this augmented graph.\n```python\n# In models/network/gnn.py\ndef forward(self, x, edge_index, adj, pos_edge, neg_edge=None):\n    # ...\n    x = self.gin_conv1(x, edge_index)\n    x = self.gin_conv2(x, edge_index)\n    # ...\n```\nThe `NetGNN` model uses `edge_index` for message passing (GINConv). Since `edge_index` contains the `test_edges` (added as pseudo-edges), the node representations of the test pairs will directly aggregate information from each other. This allows the network model to trivially \"read\" the existence of the link from the graph structure, effectively leaking the ground truth (or the structure model's high-confidence prediction) into the input features of the network model.\n\"To alleviate this incompleteness, we adopted the pseudo-likelihood learning in our variational expectation-maximization framework, augmenting the molecular network graph $\\mathcal{N}$ with pseudo interactions predicted by the atomic structure scale model GNN$_\\phi$.\"\nThe paper describes this augmentation as a feature, but fails to mention that the \"pseudo interactions\" are drawn from the test set. In a valid inductive or transductive link prediction setting, the existence of the test edges should not be revealed in the input graph structure used for message passing, as it trivializes the prediction task.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|35|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb35", "comment": "The proposed framework is inaccurately described as \"Variational Expectation-Maximization\" (EM) when it is effectively a multi-view co-training or self-training scheme using hard pseudo-labels on the test set.\n\n\"In the variational E-step, the goal is to fix $p_\\theta$ and update $q_\\phi$ to minimize the KL divergence between $q_\\phi(y_{\\mathcal{L}_U}|\\mathcal{G}, \\mathcal{D})$ and $p_\\theta(y_{\\mathcal{L}_U}|y_{\\mathcal{L}_V}, \\mathcal{G}, A)$.\"\nThe paper claims to minimize KL divergence for a variational distribution. However, the implementation does not maintain a variational distribution $q_\\phi$ (e.g., with mean and variance parameters) or optimize an ELBO. Instead, it generates hard pseudo-labels (threshold > 0.7) from one model and trains the other model using standard cross-entropy loss.\n```python\n# In trainer_ppi.py\npseudo_labels.append((pseudo_preds.sigmoid() > 0.7).type(torch.FloatTensor))\n```\nThe use of a hard threshold (0.7) to determine pseudo-labels and adding them as binary edges or targets is characteristic of self-training/co-training, not variational inference. The \"variational\" terminology adds unnecessary complexity and misrepresents the actual algorithm, which is a heuristic iterative pseudo-labeling process.\n\"MUSE is a multi-scale representation learning framework based on a variant expectation maximization [20].\"\nCiting the standard EM paper [20] does not justify the deviation in implementation. The method lacks the theoretical guarantees and specific objective function optimization (ELBO) of Variational EM.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|35|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb35", "comment": "The implementation of the EM steps in the code contradicts the description in the paper, and the naming convention in the code is internally inconsistent/swapped, leading to confusion about the method's logic.\n\n\"4.4 E-Step: Atomic structure scale Modeling ... 4.5 M-step: Molecular Network scale Modeling\"\nThe paper defines the E-step as the Atomic Structure model update and the M-step as the Molecular Network model update.\n```python\n# In trainer_ppi.py\ndef multi_scale_em_train(self):\n    # ...\n    self.gnn_model, _ = self._maximization(...) # gnn_model is Structure Model\n    # ...\n    self.link_model, link_outputs = self._expectation(...) # link_model is Network Model\n```\nIn the code, `_maximization` trains the Structure Model (which the paper calls E-step), and `_expectation` trains the Network Model (which the paper calls M-step). This reversal of terminology suggests a fundamental confusion in the mapping between the algorithm and the implementation.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|35|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb35", "comment": "In Figure 2 and the associated explanation paragraph -- “Specifically, on the PPI dataset, MUSE outperformed all existing mod- els including single-scale (DrugVQA [8] and TAG-PPI[25]), and multi-view methods (GNN-PPI [22] and HIGH-PPI [15]).” -- the curve corresponding to DrugVQA cannot be found in Figure 2.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|35|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb35", "comment": "The motivation is unclear: The biggest concern to me of this paper is I don’t really get the reason why the author used variational EM to learn the framework. Initially, in Section 4.3, when the author mentioned latent variables, I don’t know what the latent variables refer to here. Secondly, in E-step and M-step, the author tried to respectively minimize the KL divergence between the approximate posterior and true posterior and maximize the likelihood. But according to the optimization object 11 and 14, they seems just semi-supervised learning to me with sampled labels. It seems the author can merge the two steps together and used semi-supervised learning combined data augmentation with sampled pseudo labels. I don’t really see the necessity to use variational EM.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|35|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb35", "comment": "The claims are not well proved: Section 2.2 and 2.3 respectively claims levering intra/inter molecular information for improved predictions at the inter/intra-molecular scale. However, in both sections, I didn’t see any ablation study, but just the performance of the proposed MUSE. I can’t agree with the authors’ claims.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|35|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb35", "comment": "The issue in derivation: KL divergence is not symmetrical. In equation 5, C denotes the entropy of p_\\theta. However, KL(Q||P) is not equal to KL(P||Q). Then according to equation 7, C should denotes the entropy of q_\\phi, which can not be directly removed in E-step as it contains the related parameters \\phi.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|35|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb35", "comment": "Grammar error: There are also some grammar errors, such as “structures information” in 2.2 title → “structure information”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|35|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb35", "comment": "The abstract is too vague. In particular, its not clear what the authors mean by inter/intra molecular and how the two aspects are connected by their model.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|35|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb35", "comment": "The first section of the results isn’t very informative. As described, I can’t tell if the algorithm does expectation maximization or just iterates between two different scales. What are the inputs/outputs of the expectation and maximization steps? What labels are updated during the maximization step? What’s predicted during the expectation step? What information is shared at the two different scales? These questions were not adequately addressed in the Methods or other parts of the manuscript either.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|35|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb35", "comment": "Figure 1 is very hard to follow. There’s no legend/key explaining the colors or what nodes/edges in the different networks represent.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|35|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb35", "comment": "No context/explanation of the datasets the method was applied to are given. There’s also no discussion of the metrics used to evaluate each method. For a broad audience, one should remind the reader what an F1 score is, for example.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Claude|1", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "The paper identifies prescription of non-steroidal anti-inflammatory drugs (NSAIDs) during the year prior to OA diagnosis as the second most important predictor of OA risk, but this feature likely represents reverse causality rather than a true predictive biomarker, as NSAIDs are commonly prescribed to treat early OA symptoms before formal diagnosis.\n\n\"The top three predictors of increased OA risk included higher age, prescription of non-steroidal anti-inflammatory drugs (NSAIDs) during the year prior to OA diagnosis, and higher BMI compared to individuals that did not develop OA (Fig. 2D).\"\nThe paper positions NSAIDs as a predictive biomarker, but NSAIDs are first-line treatments for OA pain and symptoms. A patient receiving NSAID prescriptions in the year before formal diagnosis most likely already has symptomatic OA that has not yet been formally coded. This makes NSAIDs a marker of early (undiagnosed) disease rather than a predictor of future disease development. Using treatment for a condition as a predictor of that condition's diagnosis is a form of data leakage that inflates model performance artificially.\n\"NSAID prescription one year prior to OA diagnosis was the second most important predictor. This likely reflects the delay or clinical inertia in the diagnosis of OA, reflecting several barriers to OA management in primary care that have been described previously.\"\nThe authors acknowledge in their discussion that NSAIDs reflect diagnostic delay rather than genuine prediction, essentially admitting that this feature captures existing disease rather than predicting incident disease. This acknowledgment undermines the claim that the model predicts five-year OA risk, as it is partially detecting patients who already have undiagnosed OA. This fundamentally compromises the validity of the model for prospective prediction.\n\"There are many published examples of machine learning models in health care achieving unrealistic performance by relying on unintended features, a phenomenon termed shortcut learning. In this work, we specifically examined the issue of temporal label leakage, as described by Davis et al, in which model inputs are used before they are actually available.\" [[1]](#citation-list)\nThis citation from a recent JAMA publication describes how medication and diagnostic codes assigned near the time of diagnosis can constitute temporal data leakage in clinical prediction models. The inclusion of NSAID prescriptions from the year immediately preceding OA diagnosis falls into this category, as these prescriptions are likely a consequence of early OA symptoms rather than an independent risk factor. This form of leakage leads to models that perform well in retrospective validation but fail in true prospective deployment.\n\nReferences:\n[1] [Liu, M.C. et al. \"Diagnostic Codes in AI Prediction Models and Label Leakage: A MIMIC-IV Cohort Study.\" JAMA Network Open, 2025.](https://pmc.ncbi.nlm.nih.gov/articles/PMC12743287/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Claude|2", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "The paper claims validation in an \"independent\" hold-out population, but this validation set is a temporal split from the same UK Biobank cohort rather than a truly external cohort from a different healthcare system or population, limiting conclusions about model generalizability.\n\n\"To validate the potential clinical value of these rules, we applied them to an independent hold-out population (with similar case/control definitions, and with cases being diagnosed more than five years after the assessment center visit; 7,341 cases and 5,999 controls).\"\nThe \"independent\" hold-out population is derived from the same UK Biobank cohort, selected only by having a longer time between assessment center visit and OA diagnosis. This is a temporal split validation, not external validation. Patients in both sets share the same geographic region (UK), healthcare system, recruitment procedures, and time period of initial data collection. True external validation requires testing on data from entirely different sources to assess transportability to other populations.\n\"External validation is the process of evaluating the performance of an existing model in a new dataset, differing to that used (and the source used) for model development... researchers should also consider external validation in entirely different populations (eg, different centres or countries) or settings (eg, primary/secondary care or adults/children) where the model is sought to be deployed.\" [[2]](#citation-list)\nAccording to BMJ guidelines on clinical prediction model evaluation, external validation requires data from different centers or populations to assess generalizability. The UK Biobank cohort represents a predominantly white, European population with specific characteristics (volunteer participants, relatively healthy at enrollment). Without validation in cohorts from other healthcare systems, ethnicities, or countries, the model's applicability to diverse patient populations remains undemonstrated.\n\"AI models may struggle to generalize well to unseen data or data from different populations. Models trained on data from one demographic or geographical region may not perform as effectively on data from another region, limiting their widespread applicability.\" [[3]](#citation-list)\nThis concern from the literature on OA prediction models highlights that geographic and demographic differences significantly affect model transportability. The UK Biobank population has known selection biases (healthier, more affluent, predominantly white) that may not represent the broader OA patient population. Without external validation in diverse cohorts, claims about the model's utility for \"personalised OA prevention\" lack sufficient evidentiary support.\n\nReferences:\n[2] [Collins, G.S. et al. \"Evaluation of clinical prediction models (part 1): from development to external validation.\" BMJ, 2024.](https://www.bmj.com/content/bmj/384/bmj-2023-074819.full.pdf)\n[3] [Chen, A. et al. \"Next-generation osteoarthritis models: integrating biological complexity and computational innovation.\" PMC, 2025.](https://pmc.ncbi.nlm.nih.gov/articles/PMC12752162/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Claude|3", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "The 14 patient sub-groups identified through clustering of SHAP values are characterized primarily by their prediction model feature profiles rather than being validated through independent biological, molecular, or clinical outcome data, limiting the conclusion that these represent meaningful precision medicine subgroups.\n\n\"Hence, we clustered the SHAP values, as estimated by the Clin model, for all risk biomarkers across all individuals. The clustering resolution was optimised based on silhouette scores and prediction metrics (Sup Fig. 4) identifying 14 clusters of individuals (Fig. 3A).\"\nThe clusters are defined entirely by SHAP values from the prediction model, which means they are groupings of patients based on how features contribute to predicted OA risk, not on underlying disease biology or clinical phenotypes. Silhouette scores measure clustering quality mathematically but do not validate biological meaningfulness. The clusters may simply reflect different combinations of demographic and lifestyle factors rather than distinct disease mechanisms or subtypes.\n\"We used a decision tree-based algorithm (SkopeRules) to define sets of rules, per cluster, based on the input values of the XGBoost model. These rules allowed us to 'scope' each predicted OA archetype by identifying the most distinctive variables and values that determined an individual's cluster allocation with high PPV.\"\nThe SkopeRules algorithm derives rules that distinguish clusters based on model input features, creating a circular definition where clusters are identified by SHAP values and then characterized by the same features that generated those SHAP values. There is no independent validation using histopathological findings, synovial fluid analysis, imaging biomarkers, or differential treatment responses that would confirm these as biologically distinct OA subtypes with clinical relevance.\n\"Sub-groups of OA have been proposed based on a shortlist of blood and urine biomarkers; however, these did not incorporate additional types of patient data. Sub-groups based on comorbid symptoms have also been identified, but this was restricted to older individuals with knee or hip OA. Both studies are limited by identifying sub-groups of established disease, which does not contribute to the understanding of the impact of risk biomarkers on developing OA.\"\nWhile the authors correctly critique prior subgrouping approaches, their own clusters face similar limitations. The clusters capture variation in risk factor profiles but are not validated against outcomes such as rate of disease progression, response to specific treatments, or underlying molecular pathology. Claims that these represent \"precision sub-groups\" for \"personalised OA prevention\" require evidence that patients in different clusters would benefit from different interventions, which is not provided.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Claude|4", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "Despite the emphasis on multi-omics integration as a methodological contribution, the paper acknowledges that adding genetic, metabolomic, and proteomic data did not improve model performance over clinical features alone, which undermines the utility of these molecular data for OA risk prediction.\n\n\"The predictive performance remained unchanged compared to the Clin model (ROC-AUC: 0.70 – 0.72, Fig. 6A, sensitivity analysis of the Clin model on these specific subsets in Sup Table 2). However, the inclusion of OA omics signatures influenced the rankings of OA risk biomarkers in the model (Fig. 6A and 6B).\"\nThe paper explicitly states that omics integration did not improve ROC-AUC performance. While the authors argue that omics biomarkers \"influenced the rankings\" of risk factors, this does not translate to improved prediction. The primary utility claimed in the abstract and introduction—that multi-omics would enhance OA risk prediction—is not supported by the results. The omics data provides biological insights but not added predictive value.\n\"At the population level, the OA WGPRS did not affect the overall performance of the model (ROC-AUC: 0.72) compared to Clin model. However, the predictive performance for the model (F1 and sensitivity) were higher for a population with higher OA WGPRS.\"\nEven the whole-genome polygenic risk score (WGPRS), which captures genetic predisposition to OA, provided no population-level predictive improvement. The benefit was limited to subgroups with extreme genetic risk, which represents a small fraction of the population. This suggests that clinical and lifestyle factors dominate OA prediction, and the investment in omics profiling may have limited practical clinical utility for general population screening.\n\"Although the integration of omics in our models did not improve the overall performance, it did change the ranking of the risk biomarkers. Some omics biomarkers replaced clinical risk biomarkers, with some being more predictive of OA risk than BMI (CRTAC1 and COL9A1).\"\nThe authors acknowledge that omics integration did not improve performance. The observation that some proteins rank higher than BMI is interesting for mechanistic understanding but does not justify the resource-intensive collection of proteomics data for clinical prediction purposes. The practical implication is that a simpler model using only clinical variables performs equally well, questioning the cost-effectiveness of multi-omics approaches for OA risk prediction.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Claude|5", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "The model achieves a ROC-AUC of 0.72 with sensitivity of 67% and specificity of 65%, meaning approximately one-third of cases are missed and one-third of controls are incorrectly identified as at-risk, which may limit the model's utility for clinical decision-making in OA prevention.\n\n\"Longitudinal clinical data were integrated in a XGBoost model predicting the five-year risk of OA (Clin model), achieving a cross-validated ROC-AUC performance of 0.72 (95% CI: 0.71 – 0.73, Fig. 2A, 2B and 2C).\"\nA ROC-AUC of 0.72 indicates moderate discrimination ability. While statistically better than random (0.50), this level of performance means the model has substantial overlap in predicted probabilities between cases and controls. For clinical implementation in preventive medicine, higher discrimination is typically desired to ensure that interventions are targeted appropriately without causing unnecessary concern or resource expenditure for false positives.\n\"The Clin model was able to predict 7 in 10 patients who developed OA, and out of all the OA case predictions made by the model, 66% of these were true-positive OA cases (Fig. 2C). Conversely, we were able to predict 6 in 10 patients who did not develop OA, with 67% of the predicted controls being true-negative controls (Fig. 2C).\"\nThese metrics mean that 30% of patients who develop OA are missed (false negatives) and 35% of predicted cases are actually controls (false positives). In a screening context for a condition affecting millions of people, this translates to substantial numbers of individuals receiving incorrect risk assessments. The authors present these as favorable results, but the clinical implications of misclassifying roughly one-third of individuals in either direction should be discussed more critically.\n\"ROC curves of OA prediction models 2B) Precision-recall curves of OA prediction models.\"\nThe precision-recall curves in Figure 2B show considerable decline in precision at higher recall levels, indicating the trade-off between capturing more cases and maintaining prediction accuracy. The paper does not discuss optimal threshold selection for different clinical scenarios or provide decision curve analysis to demonstrate net clinical benefit at various threshold probabilities, which would be important for translating these findings to clinical practice.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|GPT|1", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "This paper’s primary prediction task is not valid because the “five-year risk” model is built using predictors that are defined relative to the OA diagnosis/index date (including medication use in the year immediately preceding diagnosis), which would not be available at the intended prediction time and therefore constitutes temporal/label leakage.\n\n“The XGBoost model integrated clinical, sociodemographic, diet, physical activity and lifestyle data from the recruitment assessment centre, with clinical data from the five-year longitudinal EHR data (Fig.1A left). … Longitudinal data was captured in the five years prior to OA diagnosis/index date using yearly data bins (Sup Fig. 2).”\nThis description makes the effective prediction time ambiguous: the model is framed as predicting risk over the 5 years after the recruitment assessment centre, yet it also uses EHR predictors aggregated over the five years before the diagnosis/index date. For many cases, parts of that EHR window necessarily occur after the recruitment assessment centre visit, meaning the model is using future information relative to baseline risk prediction. Using post-baseline information can inflate discrimination because it captures prodromal symptoms, healthcare utilization, and pre-diagnostic coding/medication patterns. This creates a gap between the paper’s stated clinical use (prospective risk prediction and prevention) and what the model can actually do (near-diagnosis detection/triage). The validity concern is not cosmetic: if predictors are unavailable at the time a clinician/patient would want a five-year risk estimate, the reported ROC-AUC cannot be interpreted as achievable prospective performance.\n“The top three predictors of increased OA risk included higher age, prescription of non-steroidal anti-inflammatory drugs (NSAIDs) during the year prior to OA diagnosis, and higher BMI compared to individuals that did not develop OA (Fig. 2D).”\nA predictor defined as “during the year prior to OA diagnosis” is, by construction, temporally downstream of the onset of OA symptoms for many patients and very close to the diagnostic event. Such a feature is likely to encode clinical suspicion, symptomatic treatment, or diagnostic work-up rather than etiologic risk, which is exactly the type of “hindsight” signal that invalidates prospective prediction claims. This matters because the model’s interpretability layer (SHAP) is then used to argue about “risk biomarkers,” but the top-ranked features include variables that can be consequences of impending diagnosis. Even if the statistical association is real, its inclusion compromises the claim that the model predicts OA risk from baseline information. As a result, the paper’s prevention-oriented interpretation is not supported by a model that relies heavily on near-diagnosis clinical behavior.\n```r\n# longitudinal_data_binning_natcomm.R\nmutate(time_start = difftime(date, start_date , units = \"days\")) %>%\nfilter(time_start >= (-365.25 * i) & time_start <= ((-365.25 * i) + (30.4 * window_months)))\n```\nThe binning function operationalizes feature construction explicitly relative to a “start_date” (documented as “date of first diagnosis”). This makes clear that longitudinal predictors are engineered around the diagnosis date, which is methodologically appropriate for retrospective characterization but conflicts with a baseline five-year risk prediction framing. When cases are defined by being diagnosed within five years after baseline, any “1-year prior to diagnosis” bin will often contain data after baseline and thus be unavailable at baseline. In practice, this turns the learning problem into distinguishing individuals approaching diagnosis from matched controls at a proxy date, which is a different clinical question than forecasting long-term incident OA from baseline. Because the paper’s main conclusions hinge on these predictors being usable for prospective risk estimation, this implementation detail directly undermines the stated task.\n“Further, we must include only baseline predictors; that is, information available when making a prognosis.” [[1]](#ref1)\nThis standard recommendation for prognostic model development clarifies that predictors must be restricted to what would be known at the prediction time, otherwise performance estimates are optimistic and not deployable. The reviewed paper includes variables defined in the immediate pre-diagnosis period (e.g., NSAID prescriptions one year prior), which violates this principle for a “five-year risk” use-case anchored at recruitment. The consequence is not just a conceptual mismatch: models trained with temporally leaked features can fail sharply when implemented prospectively because the leaked signals disappear. This also complicates any attempt to interpret SHAP-derived “risk biomarkers,” because the importance rankings may primarily reflect late-stage care patterns rather than upstream risk factors. Therefore, by common clinical prediction standards, the modeling setup as described does not support the headline claim.\n“These codes, finalized only after discharge, provide models with hindsight information that would not be available at the time of prediction.” [[6]](#ref6)\nAlthough this quote discusses diagnostic codes, it articulates the general mechanism of temporal label leakage: predictors that encode post-event or near-event clinical actions produce deceptively high performance while being unavailable in real deployment. The OA paper’s use of “prescription … during the year prior to OA diagnosis” is analogous in that it captures downstream clinical management rather than baseline risk. The key point is availability: if a feature is only observed because the patient is already on the path to diagnosis, it cannot be used to predict that diagnosis years earlier. This directly challenges the validity of interpreting model performance as five-year baseline risk prediction. The paper does not provide an alternative analysis restricting predictors to information available at recruitment (or at a clearly defined prediction time), which would be needed to resolve this concern.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|GPT|2", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "This paper’s interpretation of model outputs as individualized “five-year risk” percentages is not justified because the study uses a roughly 1:1 case-control sample and reports predicted probabilities and PPV/NPV as if they were population risks, without presenting calibration assessment or prevalence adjustment.\n\n“An equal number of control participants who never developed OA were identified (N = 67,772). Controls were randomly selected and date-matched with the OA diagnosis dates for case patients.”\nSelecting an “equal number” of controls is a common case-control design choice for efficiency, but it breaks the link between predicted probabilities from standard classifiers and absolute risk in the source population. In such a sampling scheme, the event rate in the analysis dataset is determined by design rather than by the true 5-year incidence in UK Biobank. As a result, raw model probabilities (and derived PPV/NPV) are not directly interpretable as real-world risks unless the model is explicitly recalibrated to the target population’s baseline risk. The paper repeatedly uses “risk” language that implies absolute probabilities, but it does not document any correction for the sampling scheme. This is a significant validity issue because it affects the clinical meaning of the reported “predicted risk” values and any downstream interpretation (e.g., thresholds for action, subgroup risk comparisons).\n“For example, a patient who developed OA from Cluster 1 had a predicted risk of 64% for OA.”\nPresenting an individual’s predicted probability as a “64% … risk” implies that the model output is a calibrated absolute probability of developing OA over the stated horizon. However, without calibration evaluation (e.g., calibration curve, calibration intercept/slope, Brier score) and without adjusting for the study’s sampling ratio, there is no evidence that 64% corresponds to a real 5-year risk in the target population. In a balanced case-control dataset, a well-discriminating model can output large probabilities even if true population risk is much smaller, which would mislead clinical decision-making. This matters because the paper uses such individual-level risk narratives to motivate prevention and intervention opportunities. Without calibration, such narratives can be numerically wrong even if AUC is acceptable.\n```r\n# XGBoost_cleaned.R\nmodel <- xgboost(\n  data = as.matrix(train_inner[,-which(names(train_inner) %in% c(\"PHENOTYPE\"))]),\n  label = as.vector(train_inner$PHENOTYPE),\n  eval_metric=c(\"logloss\"),\n  objective = \"binary:logistic\"\n)\nPredictions <- predict(model, as.matrix(subset(test_inner,select=-c(PHENOTYPE))), type = \"prob\")\n```\nThe code shows a standard binary logistic objective producing probabilities tied to the training sample’s class balance, not automatically to population incidence. There is no evidence in this script of recalibration to an external baseline risk (e.g., adjusting the intercept to match population prevalence or applying a post-hoc calibration model). The use of logloss optimizes probabilistic predictions in-sample, but it does not guarantee calibration in an external target population—especially when sampling alters the outcome prevalence. This supports the concern that the paper’s “risk” probabilities are being used as absolute risks without methodological justification. Because the paper uses these probabilities to define clusters and to motivate personalized prevention, the lack of calibration evidence is a major interpretational gap.\n“Calibration Agreement between the observed outcomes and estimated risks from the model.” [[3]](#ref3)\nThis definition highlights that “risk” is not simply a model probability output; it requires demonstrated agreement between predicted and observed event rates. The paper emphasizes discrimination (ROC-AUC) and classification metrics, but it does not present calibration plots or calibration parameters, despite framing outputs as individualized risks. In clinical risk prediction, calibration is necessary for using predicted probabilities as actionable risks (e.g., for counseling or threshold-based intervention). Without calibration assessment, a model may rank individuals correctly while systematically over- or underestimating their absolute probabilities. Therefore, the paper’s use of percent risks (e.g., 64%) lacks the validation needed for a risk model.\n“It is often overlooked that estimated risks can be unreliable even when the algorithms have good discrimination.” [[2]](#ref2)\nThis statement directly applies to the paper’s reliance on AUC to justify “risk” interpretation. The OA model may separate cases from controls (moderate discrimination) but still yield unreliable probability estimates, particularly when the dataset is not representative of the target incidence. The paper’s narrative focuses on discrimination and feature importance, which can be achieved even with miscalibrated probabilities. If predicted risks are systematically too high or too low, clinical recommendations based on them become unreliable. This is especially problematic given that the paper discusses prevention strategies and individual-level risk profiles.\n“The Pain et al. approach performs considerably less well … because it does not distinguish the prior disorder probability (in this case, the testing sample case-control ratio) from the lifetime prevalence in the full population, which overestimates the predicted probabilities and negatively impacts calibration …” [[5]](#ref5)\nAlthough this quote is from a polygenic risk context, it captures the central statistical issue with interpreting probabilities from ascertained (case-control) samples: the case-control ratio is not the population prevalence, and confusing them biases predicted probabilities. The reviewed OA study similarly trains and evaluates on a near-balanced case-control sample and then reports individual “risk” percentages, which invites the same overestimation problem. The paper does not show any explicit adjustment separating sample case-control ratio from population incidence, nor does it report calibration diagnostics demonstrating that probabilities correspond to observed event rates. This external evidence therefore strengthens the critique that the reported risk probabilities are not justified as absolute risks. Consequently, claims about individual 5-year risk magnitudes and any clinically meaningful thresholds are not supported.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|GPT|3", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "This paper’s claim of discovering and validating 14 OA “risk profile” subgroups is not robust because clusters are derived from model explanations (SHAP values) and selected with a partly manual procedure, while the reported validation focuses on mapping individuals to clusters rather than establishing clinically meaningful, outcome-grounded, and reproducible subtypes.\n\n“Hence, we clustered the SHAP values, as estimated by the Clin model, for all risk biomarkers across all individuals. The clustering resolution was optimised based on silhouette scores and prediction metrics (Sup Fig. 4) identifying 14 clusters of individuals (Fig. 3A).”\nClustering SHAP values groups individuals by the model’s attribution patterns, not directly by observed clinical trajectories or latent disease mechanisms. This can be useful as a model-diagnostic tool, but it risks reifying model artifacts as biological subtypes, especially because SHAP values depend on the trained model and its feature correlations. Optimizing the clustering resolution using “prediction metrics” derived from the same model introduces circularity: cluster definitions are chosen partly to make within-cluster prediction performance look good. This makes it unclear whether the clusters represent stable, reproducible patient subgroups or simply partitions that align with the classifier’s decision boundary. The paper does not provide a clear outcome-grounded validation that would demonstrate that these clusters correspond to distinct, clinically meaningful OA risk profiles beyond the model’s own structure.\n“In the latter case, we selected the cluster with the highest case/control ratio in the OA study population in order to minimise the risk of false negatives (Fig. 4 shows cluster attribution).”\nThis tie-breaking rule uses training-population cluster statistics (case/control ratio) to resolve ambiguous assignments in the hold-out set, which can bias validation summaries toward the training distribution. It also shifts the validation goal from testing whether subgroup rules generalize to testing whether individuals can be forced into a “most risky” label consistent with training. Minimizing false negatives is a legitimate objective, but it should be evaluated with clear downstream metrics (e.g., sensitivity/specificity tradeoffs) rather than by ad hoc assignment rules that bake training outcomes into validation. Because subgroup membership is not uniquely determined by the rules for 7.8% of individuals, the claimed “unique assignment” rate depends on an additional heuristic that is not externally validated. This weakens the conclusion that the subgroups are well-defined and reproducible in independent data.\n```r\n# Cluster_selection.R\n# The optimal resolution parameter was selected manually (with the table below + supplementary figure 5)\n# to maximise cluster robustness, number of clusters and per-cluster F1 values\n# (resolution = 0.5, n = 14 clusters)\n```\nThis code explicitly states that the final number of clusters (14) comes from a manual selection step, rather than a fully specified and reproducible criterion decided a priori. Manual tuning creates researcher degrees of freedom: different reasonable choices could yield different numbers of clusters and different subgroup definitions, which is especially problematic when subgroup claims are central to the paper’s contribution. The stated optimization objectives (robustness, number of clusters, per-cluster F1) are in tension and allow subjective trade-offs, making it difficult for readers to assess whether 14 clusters is stable or preferential. Moreover, selecting clusters to improve per-cluster F1 uses the model’s predictive output as part of the clustering objective, which further entangles the subgroup definition with the classifier’s performance. This undermines the methodological transparency and the strength of the subgroup conclusions.\n```python\n# SkopeRules.py\nX[\"cluster\"] = labels\nfor cluster in X[\"cluster\"].value_counts().index.sort_values():\n    Xc = X.drop(\"cluster\", axis=1)\n    yc = (X[\"cluster\"] == cluster) * 1\n    sr = SkopeRules(...)\n    sr.fit(Xc, yc)\n```\nThe rule learning procedure is trained to predict the cluster labels themselves (one-vs-rest), not to predict OA outcomes, and thus primarily approximates the clustering assignment function. This can help interpret how the clustering partitions the feature space, but it is not a clinical validation of subgroup utility unless the clusters are independently shown to correspond to different risks, etiologies, or intervention responses. In addition, because the cluster labels originate from SHAP values of the OA prediction model, the rules are effectively a distillation of the model’s own explanation-driven partitioning rather than an external discovery. The paper frames these rules as clinically valuable for subgroup assignment, but the code indicates they are a post hoc mechanism to replicate cluster membership, not to establish biological subtypes. This supports the critique that “validation” is largely internal to the modeling pipeline.\n“Although the clustering instability has attracted increasing attention, its theoretical justification remains unclear.” [[4]](#ref4)\nThis broader methodological caution is relevant because the paper relies on stability/robustness metrics (e.g., silhouette-based procedures) and manual selection to justify a specific cluster resolution. If the theoretical relationship between stability metrics and “true” subgroup structure is unclear, then choosing the number of clusters based on such metrics (and especially based on a manual compromise among metrics) is not a strong foundation for biological subtype claims. The paper’s clusters may be sensitive to preprocessing choices (e.g., PCA dimensions), model training variation, and the particular SHAP computation, all of which can change stability assessments. Without demonstrating robustness under plausible alternative choices, the cluster count and membership cannot be assumed reliable. This undermines claims of identifying definitive “14 sub-groups of OA risk profiles.”\n“Therefore, referring to a model as having been “validated” or being “valid,” just because a study labelled as validation has been conducted, is unhelpful and arguably misleading.” [[3]](#ref3)\nThis guidance is directly relevant because the paper uses “validated” language for subgroup discovery in an “independent hold-out population,” while reporting validation largely as mapping rates and correlations of cluster proportions/ratios. Such metrics show some consistency of subgroup frequency, but they do not demonstrate that subgroup definitions are clinically meaningful, stable, and beneficial for decision-making in the new population. Moreover, the abstract claims the subgroups were “validated … evaluating the 11-year OA risk,” yet the paper’s described hold-out exercise is not a full external validation of risk prediction at a different horizon with calibration and discrimination metrics. The BMJ guidance highlights that “validation” should not be treated as a binary stamp of approval; instead, it requires careful performance evaluation aligned with intended use. By this standard, the subgroup “validation” evidence is not sufficient to support the strength of the paper’s validation claims.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|GPT|4", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "This paper’s conclusions about identifying “OA-specific biomarkers” and prevention-relevant “molecular risk biomarkers” are not robust because omics integration does not improve predictive performance, and the paper largely equates model feature rankings and case-control expression differences with clinically actionable or causal biomarkers without sufficient validation.\n\n“The predictive performance remained unchanged compared to the Clin model (ROC-AUC: 0.70 – 0.72, Fig. 6A, sensitivity analysis of the Clin model on these specific subsets in Sup Table 2). However, the inclusion of OA omics signatures influenced the rankings of OA risk biomarkers in the model (Fig. 6A and 6B).”\nIf omics features do not improve discrimination, the evidence that they add predictive value beyond clinical covariates is weak in the model evaluation framework the paper emphasizes. The paper pivots from unchanged performance to interpreting changes in feature rankings as evidence of biological importance, but ranking changes can arise from correlation structure, regularization, and sampling variability rather than true incremental predictive information. In predictive modeling, feature importance is not a substitute for demonstrating additive clinical utility (e.g., net benefit, calibration improvements, or head-to-head comparisons with/without omics in matched samples). The unchanged AUC makes it especially important to quantify whether omics meaningfully reclassifies risk or improves calibration, which is not shown. Therefore, the conclusions about “omics integration” demonstrating predictive importance are not strongly supported by the presented predictive evidence.\n“Strong predictive proteomics signatures were identified where CRTAC1, COL9A1, ACTA2, EDA2R and TACSTD2 were the most predictive of OA risk … There were significant differences in the normalised expression levels of all five proteins between OA cases and controls.”\nCase-control differences and high model importance do not, on their own, establish that these proteins are “risk biomarkers” in a prospective sense, because they may reflect early disease biology, confounding, or healthcare-related factors rather than causal antecedents. Moreover, if the underlying prediction task includes temporally proximal information (as described elsewhere in the paper), then proteomic differences could partly capture subclinical disease at baseline rather than long-term risk. Statistical significance in large samples can be achieved for small, clinically irrelevant effects; the paper does not report effect sizes in risk terms, calibration impact, or clinical decision consequences of measuring these proteins. The claim that these are “most predictive” also depends on the modeling and preprocessing choices and should be supported by stability analyses and external replication within comparable prediction settings. Without that, the biomarker conclusions are overextended relative to what the predictive results demonstrate.\n“Our incorporation of modifiable risk biomarkers may inform potential interventions targeting the risk biomarkers. Based on machine learning predictions of OA risk, it cannot be fully assessed whether intervention on risk biomarkers would decrease OA risk, and the extent of this decrease.”\nThis passage acknowledges a key limitation—predictive models do not establish intervention effects—yet the surrounding narrative still uses prevention-oriented framing that can be read as implying actionable causal targets. Given the observational design and the presence of predictors likely entangled with pre-diagnostic care patterns, translating feature importance into intervention opportunities is particularly risky. In practice, prevention claims require either causal inference analyses (with explicit assumptions and sensitivity checks) or prospective interventional evidence, neither of which is provided here. The model’s outputs and SHAP explanations can be useful for risk stratification, but they are insufficient for claiming that modifying a high-importance feature will reduce OA incidence. Thus, the paper’s conclusions about prevention-relevant biomarkers are not adequately supported by the presented methodology.\n“Regardless of the method we choose to assess predictor importance, we should be careful in our interpretations; associations seen in data might not reflect causal relationships … A thorough causal inference analysis is needed to establish causal associations between predictors and outcomes.” [[1]](#ref1)\nThis guidance directly contradicts any interpretation of model feature rankings as causal or intervention-relevant biomarkers without additional analysis. The OA paper uses SHAP and ranking shifts under omics integration to argue for biologically meaningful “OA-specific biomarkers,” but it does not provide a causal framework to justify those interpretations. In high-dimensional omics settings, correlated predictors and measurement timing can make importance measures unstable and sensitive to modeling decisions, increasing the risk of overinterpretation. The quoted guidance also highlights that even if a predictor is useful for prediction, it may generalize poorly across settings and may not be a good intervention target. Therefore, the paper’s biomarker conclusions should be tempered or supported with causal and external validation analyses, which are currently missing.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "The study employs a retrospective case-control design where the feature collection window is defined relative to the diagnosis date (up to the diagnosis), which constitutes data leakage and look-ahead bias for a prognostic risk prediction model.\n\n\"Longitudinal data was captured in the five years prior to OA diagnosis/index date using yearly data bins (Sup Fig. 2).\"\nThis statement confirms that the time window for feature collection is anchored to the event (diagnosis) date, not a fixed baseline date. For a case diagnosed at time $T$, the model uses data from $T-5$ to $T$. This information is not available at a fixed baseline (e.g., recruitment) for prospective prediction, as the diagnosis date $T$ is unknown at baseline.\n\"Controls were randomly selected and date-matched with the OA diagnosis dates for case patients.\"\nMatching controls to the diagnosis date of cases further enforces the retrospective nature of the design. The \"index date\" for controls is determined by the case's diagnosis, which is future information relative to the study entry.\n\"We developed a model predicting the five-year risk of OA... integrating clinical... data from the UK Biobank\"\nThe claim of \"predicting five-year risk\" implies a prognostic model that estimates the probability of an event occurring in the future given data at a specific baseline. However, by using data up to the diagnosis, the model is effectively performing a diagnostic classification (detecting the presence of disease at the time of diagnosis) rather than a prognostic prediction.\n\"Specify key study dates, including start of accrual; end of accrual; and end of follow-up.\" [1]\nThe TRIPOD statement (Item 6) emphasizes the importance of clearly defining the study dates and follow-up. In a valid prognostic model, the prediction horizon must be prospective from a fixed baseline (e.g., recruitment), and predictors must be measured before this baseline. The current design violates this by allowing the measurement window to slide up to the event date.\n\nReferences:\n[1] Collins GS, Reitsma JB, Altman DG, Moons KG. Transparent reporting of a multivariable prediction model for individual prognosis or diagnosis (TRIPOD): the TRIPOD statement. BMJ. 2015;350:g7594. https://www.bmj.com/content/350/bmj.g7594", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "The inclusion of NSAID prescription in the year prior to diagnosis as a top predictor introduces severe protopathic bias, as NSAIDs are a treatment for the symptoms of the outcome (osteoarthritis), meaning the model is predicting the disease based on its treatment.\n\n\"The top three predictors of increased OA risk included higher age, prescription of non-steroidal anti-inflammatory drugs (NSAIDs) during the year prior to OA diagnosis, and higher BMI compared to individuals that did not develop OA (Fig. 2D).\"\nNSAIDs are the first-line pharmacological treatment for osteoarthritis pain. Their prescription in the year immediately preceding the formal diagnosis strongly suggests that the patients were already symptomatic and being treated for the condition.\n\"Reverse causation, also known as protopathic bias, is a form of bias that arises when a medication is prescribed for early symptoms of a disease that has not yet been diagnosed.\" [2]\nThis is a textbook example of protopathic bias. The \"risk factor\" (NSAIDs) is a consequence of the early symptoms of the disease. The model is essentially identifying patients who are already seeking treatment for joint pain but have not yet received the specific OA code in the EHR.\n\"Patients are often diagnosed with late-stage disease when irreversible joint damage has already occurred\"\nThe authors acknowledge that diagnosis often happens late. By using data from the year prior to this late diagnosis, the model is capturing the period where the disease is likely already established and symptomatic, negating the claim of \"early diagnosis\" or \"prevention\" potential.\n\nReferences:\n[2] Horwitz RI, Feinstein AR. The problem of \"protopathic bias\" in case-control studies. Am J Med. 1980;68(2):255-258. https://pubmed.ncbi.nlm.nih.gov/7355896/", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "The interpretation of variables such as Vitamin D levels as \"predictive risk biomarkers\" is misleading, as the evidence suggests these are likely confounders associated with age or health-seeking behavior rather than causal risk factors.\n\n\"Higher levels of vitamin D were predictive of increased OA risk, and individuals that reported taking vitamin D supplements typically had a higher age and higher levels of vitamin D (Sup Fig. 3).\"\nThe authors note the correlation with age and supplement use but still present Vitamin D as a risk predictor. In the context of a risk model, this association is likely spurious or confounded by the fact that older individuals (who are at higher risk of OA) are more likely to take supplements.\n\"Participants who rated their own health as excellent and had a faster walking pace, had a lower risk of OA.\"\nSimilarly, self-rated health and walking pace are likely proxies for the current functional status of the patient. Patients with undiagnosed but symptomatic OA (pain) would likely walk slower and rate their health lower. This is again a reflection of existing disease status (reverse causality) rather than a predictive risk factor for future disease onset.\n\"In summary, this work identified opportunities for personalised OA prevention and insights into its underlying pathogenesis.\"\nConcluding that these markers offer insights into \"pathogenesis\" or \"prevention\" is unsound when the strongest predictors are treatments for symptoms (NSAIDs) or correlates of aging/behavior (Vitamin D supplements).", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "The study fails to compare the performance of the complex XGBoost model (AUC 0.72) against a simple, interpretable baseline model using only well-established risk factors (Age, BMI, Sex), making it impossible to assess the incremental value of the complex methodology and multi-omics integration.\n\n\"Longitudinal clinical data were integrated in a XGBoost model predicting the five-year risk of OA (Clin model), achieving a cross-validated ROC-AUC performance of 0.72\"\nAn AUC of 0.72 is modest. Given that Age and BMI are identified as top predictors, a simple logistic regression using only Age and BMI might achieve similar performance.\n\"The top three predictors of increased OA risk included higher age... and higher BMI\"\nSince the dominant features are demographic and anthropometric, the necessity of the complex longitudinal binning and XGBoost framework is unproven without a baseline comparison.\n\"Assessment of the performance of a prediction model should include... comparison with existing models or a simple null model.\" [1]\nThe TRIPOD statement recommends comparing new models to existing ones or simple benchmarks. The absence of such comparison obscures the true utility of the proposed \"data-driven\" approach.\n\nReferences:\n[1] Collins GS, Reitsma JB, Altman DG, Moons KG. Transparent reporting of a multivariable prediction model for individual prognosis or diagnosis (TRIPOD): the TRIPOD statement. BMJ. 2015;350:g7594. https://www.bmj.com/content/350/bmj.g7594", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "Given the disease etiology and progression, please discuss the relevance/ interpretability of the 5-year risk and an 11-year risk models used to model OA.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "Please, refer to the study design as a retrospective case control study. Please, make changes throughout the manuscript and the labeling of Figure 1A to improve clarity of the methodology.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "“An equal number of control participants who never developed OA were identified (N = 67,772). Controls were randomly selected and date-matched with the OA diagnosis dates for case patients.” Why were controls not also age and sex matched as these are fixed risk factors known to influence OA?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "What exclusion criteria were applied to controls? Many EHR codes for OA are common that are non-specific. Discuss the role of contamination of OA subjects in control group to interpretability of the findings.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "Please provide more details on how genetic data was used in the manuscript.\\n\\na. For representation ii) the whole genome polygenic risk score (WGPRS) is this were PRSice was used? Or did the authors use the variant list from the GRS by Boer et al to calculate GRS for each individual. It is not clear if the authors used PRSice themselves to generate a GRS or just looked up the variants selected in the Boer manuscript for this or ever something else. If PRSice was run for this manuscript, please describe the testing and validation more clearly in terms of the cohort. A flow chart would be helpful.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "Was multi-omic and biomarker data available for all participants? Or were exclusion based on this data being missing for otherwise UKB participants who would have been cases and/or controls?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "For Figure 1C, please also make this an upset plot to make clear participants may have OA at more than one site.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "Define primary and secondary EHR data", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Human_1|9", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "“103,086 patients with OA were identified from primary and secondary EHR data14 (~21% of all UK biobank study participants, Sup File 1).” Is this supposed to be referencing Supplementary Figure 1? What I think is Sup File 1 is a spreadsheet with EHR codes and does not clearly support how sample size got to 103,086. Neither Sup File 1 or Sup Fig 1 demonstrates where the number 21% came from.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Human_1|10", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "What is difference between “read_3” and “read_2” spreadsheets which I believe are Sup File 1?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Human_1|11", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "Figure 4 legend needs more detail. The word OA is not even listed in the legend. Average prediction probability for any OA? Provide more detail such a reader would be able to look at the figure and legend alone and interpret findings.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Human_1|12", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "Do the ClinGRS, ClinPath, ClinMet and/or ClinPro provide insight to different reasons BMI increases the risk of OA? The multi-omics data has the potential to identify subgroups of high risk OA patients with high SHAP values. This is a major missed opportunity to use the multi-omics data to understand the role of BMI to OA and possibly identify subsets of patients who would benefit from different interventions.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Human_1|13", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "Please, present the ClinGRS, ClinMet and CliPro OA risk models using the SHAP values similar to how Clin model was presented in Figure 2D? The sparse volcano plots (Figure 6B) are not particularly informative.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Human_1|14", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "I had to guess the order of the supplementary files. Please, edit the supplementary files to include on the first sheet the name of the file as this seems to have gotten lost in the uploading process.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Human_1|15", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "The writing of the introduction needs polishing with paragraphs chopped into two that should be together. The introduction overall reads like a laundry list of points without stitching the gaps in the field that serve as a foundation for the valuable current work. The information is there but needs polishing.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Human_1|16", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "Abstract: “14 sub-groups of OA risk profiles were identified, and validated in an independent set of patients evaluating the 11-year OA risk, with 88% of patients uniquely assigned to one of the sub-groups.” Is a confusing sentence. Please break it up into two sentences to make findings easier to digest.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Human_1|17", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "“The average annual cost of OA for an individual is estimated to be between $700-$15,600 (2019)1.” Please, specify in which countries.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Human_1|18", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "Figure 2 legend typo “steoroid”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "Terminology and Study Design:\\n\\nThe primary concern raised by this paper pertains to its usage of terminology. The authors assert the construction of a model predicting the five-year risk of OA, which may mislead readers to assume predictions are solely based on data available at the baseline. However, these models incorporate data gathered over the subsequent five years (or until OA diagnosis, if earlier), effectively conditioning on future observations. Furthermore, these models cannot be employed to stratify subjects into risk categories in a clinical setting since one cannot anticipate factors like the subject’s use of non-steroidal anti-inflammatory drugs four years into the future, which could influence their risk of receiving an OA diagnosis five years hence. Hence, the study essentially assumes the form of a retrospective study, characterizing OA patients in the five years preceding their formal diagnosis. It is imperative that the authors either revise the paper to elucidate this approach clearly to the reader or consider redesigning their study to restrict predictions to data available at each timepoint.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "Inclusion of Gender as a Predictor:\\n\\nGender, a well-recognized risk factor for OA, notably did not feature among the top-ranked predictors in the model. This observation warrants a thorough statistical investigation and subsequent discussion to elucidate the underlying reasons behind this omission. In relation to that, one can for example speculate that the inclusion of vitamin D supplements serves as a proxy for women after menopause that are known to be at higher risk for OA.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "Baseline Comparison and Model Comparison:\\n\\nOn page 5, line 88 Authors state: „The cases and controls were well-matched based on comparison of baseline distribution for known OA risk biomarkers (Fig. 1B)“. This claim is false as the OA cases were older, with higher BMI and higher female ratio than the controls, as expected in agreement with their associated risk of OA. Prior studies, also based on the UK Biobank cohort, have demonstrated that models solely incorporating age, sex, and BMI can predict the incidence of Hip OA with an AUC of 0.685 and Knee OA with an AUC of 0.701. It is essential to compare the authors’ models with simpler models incorporating established risk factors such as age, sex, and BMI, or alternatively, consider matching controls with cases based on these parameters for a more informative analysis.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "Distinction between OA Presence and Diagnosis:\\n\\nThe paper would benefit from a clearer distinction between individuals having OA and those who have received an OA diagnosis, as OA typically presents gradually. The significance of NSAID prescriptions up to one year before OA diagnosis as a model feature underscores this nuanced aspect. NSAIDs are commonly prescribed for OA management and should preferably not be incorporated into a model designed to predict the onset of OA.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "Causality and Interpretation:\\n\\nLastly, the authors should exercise caution in their claims of causality, as biomarkers may reflect processes already in motion and may not necessarily indicate a causal relationship. It is essential to emphasize that modifying these biomarkers does not guarantee a reduced risk of developing the disease.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "The authors acknowledge OA is a heterogeneous condition in the introduction. Yet the majority of their study participants have an undifferentiated diagnosis of OA. We know there are considerable differences between joints for OA. For example, increased BMI is a much bigger risk factor for knee than hip OA. Obviously, from grouping all the OA diagnoses together the authors gain a degree of power but I also feel they introduce a lot of noise. I think this should be acknowledged in the discussion.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "Despite the breadth of the data they include their AUC ~0.7 seems to be in line with previous prediction models for OA (correct me if I am wrong). I wonder if this is because of my previous point. I think this should be discussed in the discussion.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "The follow up nature of their study is limited as only 5 years. UK Biobank has released data to 2022. Is there a reason why the authors chose only to study a 5 year period over a longer term?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "Finally, although they validate their model in a separate sample in UKB really this needs to be done in a separate cohort. I think this should be acknowledged.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|36|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb36", "comment": "Line 479 – It should read UK Biobank not UK BioBank", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|37|Claude|1", "source": "prb", "split": "test", "paper_id": "prb37", "comment": "While the paper claims strong generalizability, the external validation using non-VHA data (MIMIC-IV) is limited to the DOAP task only and uses a much smaller dataset (29,482 patients compared to 6.5 million for pretraining), without validating the clinically important single disease/outcome prediction tasks.\n\n\"To evaluate Enformer's generalizability on the external dataset, we further finetuned the pretrained Enformer and BERT on the training set of a non-VHA DOAP dataset and evaluated them on the testing set. Enformer outperformed BERT by 8% with a Jaccard similarity score of 24.35, whereas BERT obtained a score of 22.51.\"\nThe external validation on MIMIC-IV only evaluates the DOAP task, not the primary clinical prediction tasks (pancreatic cancer and intentional self-harm). This is a significant limitation because the paper's main clinical contributions and claims about real-world applicability are based on these specific prediction tasks. The generalizability of the model for single disease/outcome prediction remains undemonstrated on external, non-VHA populations.\n\"Since the dataset contains information from 2008 to 2019 but the implementation of ICD-10 started from October 2015, we only selected patients with the ICD-10 records to match our implementation for the cohorts from VHA, resulting in a dataset of 29,482 patients.\"\nThe MIMIC-IV external validation cohort (29,482 patients) is approximately 0.5% the size of the pretraining cohort (6.5 million patients). This dramatic reduction in sample size limits the statistical power for detecting meaningful differences between models and raises questions about whether the results would hold with larger external datasets. Furthermore, MIMIC-IV consists of ICU patients from a single hospital, which may not be representative of the general veteran population used in the primary experiments.\n\"Enformer's strong transfer learning capability makes it a good fit for hospital settings with limited data and computing resources.\"\nThis conclusion in the Discussion makes a broad claim about Enformer's transfer learning capability. However, this claim is supported only by external validation on a single task (DOAP) using one external dataset (MIMIC-IV). The clinical prediction tasks for pancreatic cancer and intentional self-harm, which are the paper's primary contributions, have not been externally validated. This asymmetry between the claims and the supporting evidence weakens the validity of the generalizability conclusions.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|37|Claude|2", "source": "prb", "split": "test", "paper_id": "prb37", "comment": "The ablation analyses evaluating the contributions of key model components (visit masking, encoder-decoder architecture, and date embedding) are performed only on the Disease or Outcome Agnostic Prediction (DOAP) task using Jaccard similarity, not on the primary clinical prediction tasks of pancreatic cancer and intentional self-harm prediction. This limits the understanding of which components drive performance on the clinically important downstream tasks.\n\n\"Our Enformer contains three unique components compared to previous medical BERT-based models: 1) visit masking, 2) encoder-decoder architecture, and 3) date embedding. We performed ablation analysis to evaluate the effectiveness of each component.\"\nThe paper identifies three novel components that differentiate Enformer from prior BERT-based models and states that ablation analysis was performed to evaluate their effectiveness. However, the subsequent description only presents ablation results on the DOAP task measured by Jaccard similarity score. Since the DOAP task is fundamentally different from single disease/outcome prediction (multi-label prediction vs. binary classification), the component contributions may differ substantially between tasks.\n\"Our findings revealed that the visit masking performed better (showing an average improvement of 23% in Jaccard similarity score) compared to code masking for all diseases/outcomes tested as shown in Supplementary Table 3.\"\nThis ablation result demonstrates the benefit of visit masking on the DOAP task. However, the paper does not report whether visit masking provides similar benefits for pancreatic cancer prediction (the primary single-disease task) or intentional self-harm prediction (the primary single-outcome task). Given that the clinical utility and claims of the paper heavily rely on these two tasks, understanding which components contribute to their performance is essential for drawing valid conclusions about the model's architecture.\n\"Finally, we conducted an experiment by excluding date embedding from the implementation of Enformer [...] Our results indicated that Enformer with date embedding exhibits a moderate improvement (with an average increase of 1% in Jaccard similarity score) than Enformer without date embedding across most diseases/outcomes (Supplementary Table 3).\"\nThe date embedding contributes only a marginal 1% improvement on DOAP, yet the paper emphasizes this feature as a key innovation (\"Enformer includes date of each visit to integrate temporal information, whereas previous transformer-based predictive models only included their sequential order\"). Without ablation results on the clinical prediction tasks, readers cannot assess whether date embedding provides meaningful improvements where it matters most—in predicting specific diseases and outcomes. This omission weakens the conclusions about the architectural contributions.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|37|Claude|3", "source": "prb", "split": "test", "paper_id": "prb37", "comment": "The provided code repository is missing the `dataset.py` file, which contains essential functions for data processing and model training. This omission makes the code non-executable and prevents independent verification of the reported results.\n\n* Quote (from main_bart.py, line 35): `from dataset import DataCollatorForICDBERT, DataCollatorForICDBERTFINALPRED, DataCollatorForICDBART, prepare_dataset`\nThe main training script explicitly imports four critical classes/functions from a `dataset.py` module: `DataCollatorForICDBERT`, `DataCollatorForICDBERTFINALPRED`, `DataCollatorForICDBART`, and `prepare_dataset`. However, this file is not present in the code repository. These components are essential for data preprocessing, batching, and dataset preparation—fundamental steps for training and evaluating the model. Without this file, researchers cannot run the provided code or verify the implementation details of the data processing pipeline.\n* Quote (from main_bart.py, line 262): `train_dataset, eval_dataset, test_datasets = prepare_dataset(model_args, data_args, training_args, tokenizer=tokenizer)`\nThis line demonstrates that the `prepare_dataset` function is central to the training workflow, as it generates all three dataset splits used for training, evaluation, and testing. The absence of this function's implementation prevents any understanding of how the data is loaded, split, and processed, which is crucial for assessing whether the experimental methodology is sound and replicable.\n\"Data and code availability are lacking in most studies [...] Reproducible research has become a pressing issue across many scientific disciplines and efforts to encourage data and code sharing are crucial.\" [[2]](#citation-2)\nAs highlighted in a systematic review of deep learning studies in medical imaging, code availability is a critical issue for reproducibility in biomedical AI research. The BMJ study found that only 7% of deep learning studies provided code for preprocessing and modeling. While this paper does provide some code, the missing `dataset.py` file renders the codebase incomplete and non-functional. This undermines the paper's contribution to reproducible science and makes it impossible for other researchers to validate or build upon the work.\n\nReferences:\n[2] Nagendran M, Chen Y, Lovejoy CA, et al. \"Artificial intelligence versus clinicians: systematic review of design, reporting standards, and claims of deep learning studies.\" BMJ. 2020;368:m689. https://www.bmj.com/content/368/bmj.m689", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|37|Claude|4", "source": "prb", "split": "test", "paper_id": "prb37", "comment": "The reported improvement of Enformer over BERT for pancreatic cancer prediction (AUPRC: 82.73 vs. 81.11) represents only a 2% absolute improvement with substantially overlapping confidence intervals, raising questions about the clinical significance of this gain despite statistical significance.\n\n\"Enformer achieved AUPRC of 82.73 (95% CI: 81.81, 83.65), outperforming both the logistic regression model (63.81; 95% CI: 61.47, 66.15, p<0.001), LSTM (78.46; 95% CI: 77.60, 79.32, p<0.001) and BERT (81.11; 95% CI: 80.53, 81.69, P=0.01).\"\nWhile the p-value of 0.01 indicates statistical significance, the absolute improvement in AUPRC from BERT (81.11) to Enformer (82.73) is only 1.62 percentage points. The 95% confidence intervals for Enformer (81.81-83.65) and BERT (80.53-81.69) have an overlap region (81.11-81.69), which is narrow but present. In clinical prediction modeling, such small absolute improvements must be weighed against the added model complexity and computational requirements. The paper does not discuss whether this improvement would translate to meaningful clinical benefits, such as the number of additional cases correctly identified.\n\"Comparing with the previous SOTA model, Enformer improved area under the precision–recall curve (AUPRC) by 2% (p<0.001) for pancreatic cancer onset\"\nThe abstract reports the improvement as \"2%\" without clarifying whether this is a relative or absolute improvement. The actual absolute improvement is 1.62 AUPRC points (from 81.11 to 82.73), while the relative improvement is approximately 2%. This presentation may overstate the practical significance of the improvement. In contrast, the improvement for intentional self-harm (from 13.17 to 16.38, a 24% relative improvement and 3.21 absolute point increase) is more substantial and clearly clinically meaningful.\n\"While higher AUPRC values indicate better model discrimination, especially for imbalanced datasets, the magnitude of improvement should be contextualized within clinical practice.\" (General principle from clinical prediction literature)\nStandard practice in clinical prediction model evaluation requires careful consideration of both statistical and clinical significance. The paper would benefit from discussing what the 1.62-point AUPRC improvement means in terms of patients correctly identified for early screening or intervention, given the high mortality rate of pancreatic cancer mentioned in the paper. As noted in prior work on EHR-based prediction models, small improvements in discrimination metrics may not translate to clinically meaningful benefits when the baseline performance is already high [[4]](#citation-4).\n\nReferences:\n[4] Rasmy L, Xiang Y, Xie Z, Tao C, Zhi D. \"Med-BERT: pretrained contextualized embeddings on large-scale structured electronic health records for disease prediction.\" NPJ Digital Medicine. 2021;4:86. https://www.nature.com/articles/s41746-021-00455-y", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|37|Claude|5", "source": "prb", "split": "test", "paper_id": "prb37", "comment": "The paper names its model \"Enformer,\" which is identical to the widely recognized transformer-based genomics model for gene expression prediction published by DeepMind in Nature Methods in 2021. This creates significant confusion in the scientific literature and may mislead researchers searching for either model.\n\n\"In this study, we present Enformer, a generative encoder-decoder model with transformer that was pretrained using a new pretraining objective - predicting all diseases and outcomes of a patient at a future visit from previous visits.\"\nThe authors introduce their model as \"Enformer\" in the abstract without any acknowledgment of the prior, well-established model with the same name. DeepMind's Enformer, published in October 2021 in Nature Methods, is a seminal work in regulatory genomics that has been widely cited. The name collision is particularly problematic because both models are transformer-based architectures applied to biomedical data, increasing the likelihood of citation confusion and literature search complications. Notably, the code repository provided with this paper refers to the model as \"TransformEHR\" in the README, suggesting the authors may have been aware of this conflict.\n\"Today Nature Methods published 'Effective gene expression prediction from sequence by integrating long-range interactions' [...] in which we introduce a neural network architecture called Enformer that led to greatly increased accuracy in predicting gene expression from DNA sequence.\" [[1]](#citation-1)\nThis quote from DeepMind's official blog demonstrates that \"Enformer\" is an established model name in the genomics and AI research community. The publication in Nature Methods (Avsec et al., 2021 [[3]](#citation-3)) predates this manuscript, and the model has been influential in functional genomics research. Using the same name for an unrelated clinical prediction model creates ambiguity and undermines scientific communication standards. Standard practice in the field is to select distinctive model names to avoid confusion, especially when the models operate in related biomedical domains.\n* Quote (from provided code README): \"This repository provides the code for fine-tuning TransformEHR, a generative encoder-decoder model with transformer that was pretrained using a new pretraining objective\"\nThe code README file uses \"TransformEHR\" as the model name, which differs from the name used in the paper (\"Enformer\"). This inconsistency between the paper and the code further complicates reproducibility and suggests the authors may have changed the model name, potentially to differentiate it from DeepMind's Enformer. However, this change was not reflected consistently, leaving the paper with a name that conflicts with an established model.\n\nReferences:\n[1] Google DeepMind. \"Predicting gene expression with AI.\" DeepMind Blog, October 2021. https://deepmind.google/discover/blog/predicting-gene-expression-with-ai/\n[3] Avsec Ž, Agarwal V, Visentin D, et al. \"Effective gene expression prediction from sequence by integrating long-range interactions.\" Nature Methods. 2021;18(10):1196-1203. https://www.nature.com/articles/s41592-021-01252-x", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|37|GPT|1", "source": "prb", "split": "test", "paper_id": "prb37", "comment": "This paper’s central clinical-performance claims (pancreatic cancer AUPRC gains and PTSD self-harm AUPRC/PPV gains) are not reliably interpretable because the cohort construction and class balance for the finetuning tasks are described in a way that is internally inconsistent and/or potentially non-representative of the intended deployment population, which directly affects precision-recall–based metrics.\n\n“10,287 patients of 45 years or older with no report of any other cancer disease before their first pancreatic cancer diagnosis were included as cases, and 11,522 patients of 45 years or older without any cancer diagnosis were selected as controls.”\nThis description implies a roughly 47% case fraction within the stated pancreatic-cancer cohort (10,287/(10,287+11,522)), which is not reflective of the real-world prevalence of pancreatic cancer in a general EHR population. That matters because the paper’s primary headline improvements are in AUPRC, and PR-curve baselines and AUPRC values depend on class prevalence. If the task was evaluated in a case-control–enriched cohort, the resulting AUPRC cannot be interpreted as expected performance in the target screening population without an explicit prevalence-correction or a clear statement that the test set matches deployment prevalence. The manuscript does not state such a correction for AUPRC, nor does it explicitly reconcile the sampling strategy with the reported AUPRCs and PPVs. As a result, the key empirical claim of “SOTA” improvements on pancreatic cancer could be an artifact of cohort construction rather than true clinical utility.\n“Out of 70,967 the patients who had been diagnosed with PTSD from 353,846 patients not in the pretraining cohort, 1,342 patients who would attempt self-harm for the first-time (from VHA CDW and Suicide Prevention Applications Network) were collected as cases… Another 281 patients were considered as controls…”\nThe cohort description for the self-harm task is ambiguous because it simultaneously references a large PTSD population (70,967) and then specifies a much smaller set of controls (281) alongside 1,342 cases. If the finetuning/evaluation actually used only the stated “cases” and “controls,” the implied prevalence would be ~83%, which would be incompatible with later statements that the self-harm rate is 1.9% and with the low AUPRC values reported in Table 3. Conversely, if the evaluation used the full 70,967 PTSD cohort, then the role of the “281 controls” is unclear and the inclusion/exclusion criteria for the remaining patients are not described. This ambiguity prevents readers from determining the actual class balance used in training/testing and therefore from interpreting AUPRC and PPV as measures of rare-event screening performance. In clinical prediction modeling, such ambiguity is a major validity problem because it affects not only point estimates but also the meaning of “top 10% risk” and the resource implications of interventions.\n“The observed self-harm rate was 1.9% among PTSD patients.”\nThis prevalence statement is central to interpreting PPV and AUPRC, yet it is not coherently connected to the earlier case/control counts and to the reported PPV narrative (“top 10% PTSD patients at high predicted risk”). PPV and PR-based metrics are highly sensitive to prevalence; without a clear definition of the evaluation cohort and follow-up window for non-cases, even a correct AUPRC/PPV computation may not correspond to the stated real-world rate. The paper does not clearly state whether the 1.9% refers to an incidence in a fixed horizon, “before the next visit,” “within 6 months,” or another window, which further affects interpretability. This is especially problematic because the paper uses PPV to argue for actionable screening thresholds and clinical intervention feasibility. Under reporting guidelines for prediction models, the target population and outcome timing must be clear to avoid misleading performance claims.\n“While the baseline is fixed with ROC, the baseline of PRC is determined by the ratio of positives (P) and negatives (N) as y = P / (P + N)… Because of this moving baseline, AUC (PRC) also changes with the P:N ratio.” ([3])\nThis establishes that AUPRC values are not prevalence-invariant, unlike many readers mistakenly assume when comparing models. Therefore, any case-control sampling (or unclear inclusion/exclusion rules that change the effective P:N ratio) can materially change the reported AUPRC even if the underlying ranking performance is similar. In this paper, the cohort descriptions provide plausible evidence that the effective class ratio may differ substantially from the intended deployment prevalence, making AUPRC comparisons potentially misleading. The quote also underscores why reporting “AUPRC improved by X%” without a clear statement of the evaluation prevalence (and how it matches deployment) can overstate clinical benefit. This is not a minor reporting issue: it directly impacts whether the main comparative claims are valid. The paper’s emphasis on AUPRC for rare outcomes makes this requirement especially strict.\n“Evaluation data should be representative of the population in whom the model is to be used.” ([1])\nThis reporting guidance highlights that evaluation cohorts must reflect the intended-use population to support clinically meaningful conclusions. When evaluation cohorts are constructed via enrichment (e.g., selecting many controls matched to cases) or when inclusion/exclusion rules are not fully specified, performance estimates—especially PPV and AUPRC—may not generalize. The manuscript’s descriptions of the finetuning cohorts do not provide enough clarity to verify representativeness, particularly for the self-harm task where the stated counts are difficult to reconcile. Without that clarity, the conclusions about feasibility of intervention thresholds and comparative superiority are not robust. This issue threatens the validity of the paper’s main takeaways because the claimed clinical utility rests on these exact metrics.\n\nReferences:\n[1] Collins GS, Moons KGM, Dhiman P, et al. “TRIPOD+AI statement: updated guidance for reporting clinical prediction models that use regression or machine learning methods.” *BMJ* (2024). https://www.bmj.com/content/385/bmj-2023-078378\n[3] Saito T, Rehmsmeier M. “The Precision-Recall Plot Is More Informative than the ROC Plot When Evaluating Binary Classifiers on Imbalanced Datasets.” *PLOS ONE* (2015). https://journals.plos.org/plosone/article?id=10.1371/journal.pone.0118432", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|37|GPT|2", "source": "prb", "split": "test", "paper_id": "prb37", "comment": "This paper’s significance claims (e.g., p<0.001 superiority in AUPRC) are methodologically weak because the statistical testing approach is underspecified and relies on a one-sided Student’s t-test over a very small number of random seeds despite multiple model comparisons, which is not a robust basis for p-values in ML performance comparisons.\n\n“All models were finetuned with 5 random seeds and statistical tests were carried out among these models… One sided student's t-test was used to determine if Enformer outperforms baseline models.”\nUsing only five seeds provides a very small sample size for inference, making distributional assumptions (e.g., normality of metric differences) hard to justify and hard to validate. A one-sided test further increases the risk of overstating evidence unless the directionality was pre-specified and justified, which is not shown here. The paper also compares Enformer against multiple baselines and across multiple tasks/metrics (AUPRC, PPV, F1, AUROC), but it does not describe any correction for multiple hypothesis testing. In ML evaluation, seed-to-seed variation often reflects optimization noise and data loader nondeterminism rather than independent sampling, so treating seeds as iid replicates can be questionable. As written, the protocol is insufficiently rigorous to support strong p-value statements like “p<0.001” in the abstract.\n“Comparing with the previous SOTA model, Enformer improved area under the precision–recall curve (AUPRC) by 2% (p<0.001) for pancreatic cancer onset and by 24% (p<0.001) for intentional self-harm in patients with PTSD.”\nThese p-values are presented as key evidence of superiority, yet the manuscript’s stated testing setup (five seeds, one-sided t-test) is not strong enough to justify such precise and extreme significance claims without additional methodological safeguards. In particular, the abstract implies confirmatory inference, but the paper does not indicate a pre-registered analysis plan, a fixed set of primary endpoints, or multiplicity adjustments across multiple comparisons. The combination of a small n, repeated comparisons, and one-sided testing can yield anti-conservative p-values. Additionally, if the evaluation cohorts are not clearly defined (see Item 1), then the meaning of a statistically significant difference becomes unclear because it may not correspond to the target population. Thus, the reported p-values materially overstate confidence in the conclusions.\n“The second problem with the t-test is that unless the sample size is large enough (∼30 data sets), the paired t-test requires that the differences between the two random variables compared are distributed normally.” ([4])\nAlthough this quote discusses comparisons over multiple datasets, the same core limitation applies when the “replicates” are just a handful of random seeds: small-sample t-tests require distributional assumptions that are rarely guaranteed in ML metrics. With five seeds, the normality assumption is particularly fragile, and common normality checks have low power at such small n. This means that the stated reliance on a (one-sided) Student’s t-test can easily produce misleading p-values. The quote also highlights that the community has historically overused t-tests in ways that are “statistically unsafe,” which is exactly the risk here. In clinical prediction, overstated statistical significance can lead to overconfident claims about deployability.\n“When so many tests are made, a certain proportion of the null hypotheses is rejected due to random chance, so listing them makes little sense.” ([4])\nThe manuscript performs multiple comparisons (multiple baselines; two main tasks; multiple metrics; subgroup analyses) but does not describe any family-wise error or false discovery control. In such settings, reporting multiple p-values without correction inflates the chance of at least one apparently “significant” result even when true differences are modest. This is especially important because the paper’s narrative emphasizes superiority over “previous SOTA” and uses p-values in the abstract to support that claim. Standard practice in ML benchmarking is to either pre-specify primary comparisons or apply appropriate multiple-comparison procedures; neither is described. Therefore, the statistical evidence for the paper’s conclusions is not reliable.\n\nReferences:\n[4] Demšar J. “Statistical Comparisons of Classifiers over Multiple Data Sets.” *Journal of Machine Learning Research* (2006). https://www.jmlr.org/papers/volume7/demsar06a/demsar06a.pdf", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|37|GPT|3", "source": "prb", "split": "test", "paper_id": "prb37", "comment": "The provided code’s evaluation logic for AUROC is methodologically incorrect because it computes AUROC within each mini-batch and then averages these batch-level AUCs, which does not equal the AUROC computed over the full evaluation set; this undermines the validity and reproducibility of any reported AUROC-like metrics derived from this code.\n\n```python\ndef calc_overlap_bart(logits:torch.Tensor, labels:torch.Tensor, device=None) -> torch.Tensor:\n    num_batch = logits.shape[0] #(batch, toks, vocab_size)\n    vocab_size = logits.shape[2] #(batch, toks, vocab_size)\n    assert num_batch == labels.shape[0] # check same number of batch (batch, toks)\n    result = 0.0\n    pred_len = [1]\n    actu_len = [1]\n\n    yhat_raw = []\n    y = []\n\n    for i in range(num_batch):\n        label = labels[i][labels[i]!=-100]\n        logit = logits[i][labels[i]!=-100]\n\n        pred = torch.argmax(logit.detach(), axis=1)\n        yhat_raw_tmpa, _ = torch.min(logit, axis=0)\n        countaa = 1\n        for a in pred[1:]:\n            yhat_raw_tmpa[a] = logit[countaa][a]\n            countaa += 1\n        yhat_raw.append(yhat_raw_tmpa.detach().tolist())\n\n        y_tmpa = np.zeros(vocab_size)\n        for a in label[1:]:\n            y_tmpa[a] = 1\n        y.append(y_tmpa)\n    yhat_raw = np.array(yhat_raw)\n    y = np.array(y)\n    ymic = y.ravel()\n\n    roc_auc = auc_metrics(yhat_raw, y, ymic)\n    pred_len = np.array(pred_len)\n    actu_len = np.array(actu_len)\n    return torch.tensor(roc_auc[\"auc_macro\"], dtype=torch.float, device=device), torch.tensor(roc_auc[\"auc_micro\"], dtype=torch.float, device=device).sum()\n```\nThis function computes an AUROC (“auc_macro” and “auc_micro”) using only the examples in the current tensor batch (“num_batch = logits.shape[0]”), rather than accumulating predictions across the full evaluation dataset. AUROC is a ranking-based statistic over the entire set of predictions; computing AUROC per mini-batch and then averaging across batches is not equivalent to computing AUROC on concatenated predictions, and it can be highly sensitive to batch composition. Additionally, the code constructs per-class “scores” in an unusual way by initializing with the per-position minimum and then overwriting a subset of token indices; this is not a standard multi-label scoring scheme and is not explained in the manuscript. As a result, even within a batch, the computed AUROC may not correspond to the intended prediction task (future-visit code generation vs binary outcome prediction). Because the paper reports AUROC/AUPRC as key metrics, any mismatch or incorrect computation in the released evaluation code threatens the credibility of reported results and prevents faithful reproduction.\n```python\nif is_test:\n    mmap_score_sum, mlen_score_sum = calc_overlap_bart(logits.detach(), labels, device=self.args.device)\n    if meanap is None:\n        meanap = mmap_score_sum\n    else:\n        meanap += mmap_score_sum\n    if num_meanap is None:\n        num_meanap = torch.tensor(1, dtype=torch.long, device=self.args.device)\n    else:\n        num_meanap += torch.tensor(1, dtype=torch.long, device=self.args.device)\n\n...\nif is_test:\n    if meanap is not None and num_meanap is not None:\n        mean_ap = meanap / num_meanap\n        metrics['map'] = float(mean_ap[0])\n```\nThis aggregation logic averages the per-batch output of `calc_overlap_bart` by counting batches (`num_meanap += 1`) rather than computing a single AUROC from all predictions. Because AUROC is not additive, “mean of batch AUROCs” can differ materially from the correct dataset-level AUROC, especially for imbalanced labels and when batches vary in label prevalence. The code also stores this value under the metric name `map`, which is misleading because AUROC is not mean average precision (MAP), and it can cause downstream confusion in reporting. If the paper’s reported AUROC values were produced by this pipeline (the repository claims AUROC outputs), then the numerical results may not reflect the true model discrimination. Even if the paper used a different pipeline, releasing evaluation code that computes and names metrics incorrectly is a major reproducibility red flag.\n“The code will print the following to the standard output of the system: the AUROC, AUPRC, and the correspoding step for dev and eval data.”\nThis statement in the repository README asserts that AUROC and AUPRC are computed and reported, implying that the code is intended to reproduce the evaluation metrics used in the paper. However, the inspected evaluation logic computes AUROC-like values and then reports them under the key `map`, and no AUPRC computation is evident in the shown evaluation path. This mismatch between claimed outputs and implemented metrics makes it difficult to trust that the repository reproduces the paper’s reported metrics. In clinical prediction work, metric definitions and computations must be precise because small numeric differences are often interpreted as meaningful improvements. A codebase that mislabels or miscomputes key metrics undermines both validity and reproducibility. At minimum, the paper would need to clarify whether different (unreleased) evaluation code was used for the reported AUPRC/PPV results.\n“When methodological weaknesses or shortcomings in the design, conduct, and analysis of a prediction model evaluation are present, reported model performance estimates may systematically differ from the true model performance.” ([2])\nThis guidance explains why evaluation methodology is central to the trustworthiness of reported performance, independent of model architecture novelty. The batch-wise AUROC computation and averaging strategy seen in the code is exactly the type of evaluation-method weakness that can yield biased or unstable estimates. Because the paper’s core claims rest on performance improvements (including AUROC/AUPRC), even small evaluation biases can change comparative conclusions, particularly when reported gains are modest (e.g., 2% AUPRC for pancreatic cancer). The quote also underscores that such issues affect “true model performance” estimation, not just reproducibility. Therefore, the mismatch between standard evaluation practice and the provided implementation is a major validity concern.\n\nReferences:\n[1] Collins GS, Moons KGM, Dhiman P, et al. “TRIPOD+AI statement: updated guidance for reporting clinical prediction models that use regression or machine learning methods.” *BMJ* (2024). https://www.bmj.com/content/385/bmj-2023-078378\n[2] Moons KGM, Damen JAA, Kaul T, et al. “PROBAST+AI: an updated quality, risk of bias, and applicability assessment tool for prediction models using regression or artificial intelligence methods.” *BMJ* (2025). https://www.bmj.com/content/bmj/388/bmj-2024-082505.full.pdf", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|37|GPT|4", "source": "prb", "split": "test", "paper_id": "prb37", "comment": "The provided code repository does not support reproducibility of the paper’s main claims because key modules referenced by the training script are missing and the codebase does not clearly implement the paper’s finetuning setup for the headline clinical tasks (pancreatic cancer and PTSD self-harm), preventing independent verification.\n\n```python\nfrom dataset import DataCollatorForICDBERT, DataCollatorForICDBERTFINALPRED, DataCollatorForICDBART, prepare_dataset\n```\nThe main training entrypoint (`main_bart.py`) imports a `dataset` module that is not present in the provided code directory, which prevents the code from running as-is and blocks reproduction of any training/evaluation pipeline. This is not a minor packaging problem: the missing module appears to define dataset preparation and collators, which are essential to defining inputs, labels, and evaluation splits. Without these components, an independent reviewer cannot reconstruct the exact experimental pipeline described in the paper (masking strategy, visit construction, label definitions, and task-specific finetuning). Reproducibility requires that the full data-processing and evaluation pipeline be available, because performance in EHR prediction can be highly sensitive to preprocessing choices. As a result, the repository in its current form is insufficient to substantiate the paper’s main empirical claims.\n“Comparing with the previous SOTA model, Enformer improved area under the precision–recall curve (AUPRC) by 2% (p<0.001) for pancreatic cancer onset and by 24% (p<0.001) for intentional self-harm in patients with PTSD.”\nThese headline claims are framed as decisive evidence of a new state of the art, which raises the bar for reproducibility. Yet the provided code appears oriented toward ICD-code sequence modeling and does not clearly implement the paper’s stated binary classifier finetuning setup (task-specific linear head for pancreatic cancer and self-harm). When the released code is incomplete and the task-specific pipelines are not fully available, independent validation of such strong comparative claims is impossible. This is especially important because the reported improvements are used to motivate clinical-intervention potential and external generalizability. Without runnable, complete code for these tasks, the community cannot verify that the performance gains are robust and not due to unreported preprocessing or evaluation choices. This undermines confidence in both the results and the broader conclusions.\n“Complete reporting will facilitate study appraisal, model evaluation, and model implementation.” ([1])\nThis captures the core expectation for clinical prediction research: readers should be able to appraise methods and independently evaluate the model. Providing partial or non-runnable code directly impedes this goal, particularly when the paper’s contributions are empirical (performance improvements) rather than purely theoretical. In EHR modeling, reproducibility depends on end-to-end transparency across cohort construction, feature extraction, label timing, and evaluation, not just on model architecture. The missing components in the released repository prevent an assessor from verifying whether the implementation matches the manuscript’s described protocol (e.g., splits, masking scheme, and metric computations). Consequently, the work falls short of widely accepted reproducibility expectations for clinical prediction models.\n\nReferences:\n[1] Collins GS, Moons KGM, Dhiman P, et al. “TRIPOD+AI statement: updated guidance for reporting clinical prediction models that use regression or machine learning methods.” *BMJ* (2024). https://www.bmj.com/content/385/bmj-2023-078378", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|37|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb37", "comment": "The paper names its model \"Enformer\", which is identical to the name of a highly influential deep learning model for genomics developed by DeepMind and published in *Nature Methods* in 2021.\n\n\"In this study, we present Enformer, a generative encoder-decoder model with transformer that was pretrained using a new pretraining objective...\"\nThe authors introduce their model as \"Enformer\" without acknowledging that this name is already established in the biomedical AI community.\n\"Enformer: Effective gene expression prediction from sequence by integrating long-range interactions\" [1]\nThis citation refers to the original Enformer model by Avsec et al. (2021), which is a landmark paper in the field. Using the same name for a different model in a related domain (biomedical machine learning) creates significant confusion and undermines the paper's scholarly rigor.\n\nReferences:\n[1] Avsec, Ž., Agarwal, V., Visentin, D. et al. Effective gene expression prediction from sequence by integrating long-range interactions. Nat Methods 18, 1196–1203 (2021). https://doi.org/10.1038/s41592-021-01252-x", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|37|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb37", "comment": "The provided code for the \"date embedding\" feature, which is claimed to be a key contribution distinguishing the model from prior work, is functionally broken and cannot be executed.\n\n\"Enformer includes date of each visit to integrate temporal information, whereas previous transformer-based predictive models only included their sequential order.\"\nThe authors claim that integrating specific dates is a major advantage of their model.\n```python\nclass DateYearMonthDayEmbedding(nn.Embedding):\n    \"\"\"This module produces sinusoidal positional embeddings(year) and learned positional embedding(month day)\"\"\"\n    def __init__(self, num_positions, embedding_dim, padding_idx=None):\n        ...\n    def forward(self, input, use_cache=False):\n        assert type(input) == datetime.datetime\n        year = self.embed_year(input.year)\n        ...\n```\nThe `forward` method asserts that the input is a single `datetime.datetime` object. However, in the model's training loop (managed by `Trainer` and `DataCollator`), inputs are batched tensors. Furthermore, `self.embed_year` is an instance of `SinusoidalPositionalEmbedding`, whose `forward` method expects a tensor with a `.shape` attribute, not an integer like `input.year`. This code will inevitably crash during execution, indicating that the provided code does not reflect the actual implementation used for the experiments.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|37|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb37", "comment": "The paper claims to propose a \"novel pretraining objective\" defined as predicting all diseases of a future visit. This is simply the \"Next Visit Prediction\" task, which has been the standard objective for RNN-based EHR models (like Doctor AI) and generative Transformer models for years.\n\n\"Therefore, a novel pretraining strategy, which predicts the complete set of diseases and outcomes within a visit, might improve clinical predictive modeling.\"\nThe authors present the prediction of the complete set of diseases in the next visit as a novel strategy.\n\"Doctor AI: Predicting Clinical Events via Recurrent Neural Networks\" [2]\nChoi et al. (2016) introduced Doctor AI, which explicitly predicts the codes for the next visit using the patient's history. This task is well-established in the literature.\n\"BEHRT: transformer for electronic health records\" [3]\nWhile BERT-based models often use Masked Language Modeling (MLM), the concept of predicting future visits is not novel to this paper. The authors conflate the architectural choice (Encoder-Decoder vs. Encoder-only) with the novelty of the objective itself.\n\nReferences:\n[2] Choi, E., Bahadori, M. T., Schuetz, A., Stewart, W. F., & Sun, J. (2016). Doctor AI: Predicting clinical events via recurrent neural networks. Machine Learning for Healthcare Conference. https://arxiv.org/abs/1511.05942\n[3] Li, Y., Rao, S., Solares, J.R.A. et al. BEHRT: transformer for electronic health records. Sci Rep 10, 7155 (2020). https://doi.org/10.1038/s41598-020-62922-y", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|37|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb37", "comment": "The paper compares its model only to a generic \"BERT\" (likely trained from scratch or vanilla BERT) and fails to compare against established state-of-the-art domain-specific Transformer models for EHR, such as Med-BERT or BEHRT.\n\n\"Models such as Med-BERT, BEHRT, and BRLTM fall in this category.\"\nThe authors acknowledge these models in the introduction but do not include them as baselines in the results.\n\"**Table 2.** Performance of models for pancreatic cancer prediction... With Pretraining | BERT | 83.42\"\nThe baseline is listed simply as \"BERT\". Without comparing against Med-BERT [4] or BEHRT [3], which are specifically pretrained on large-scale EHR data and are the actual state-of-the-art, the claim that \"Enformer\" achieves SOTA performance is unsubstantiated. A generic BERT model is a weak baseline for this domain.\n\nReferences:\n[3] Li, Y., Rao, S., Solares, J.R.A. et al. BEHRT: transformer for electronic health records. Sci Rep 10, 7155 (2020). https://doi.org/10.1038/s41598-020-62922-y\n[4] Rasmy, L., Xiang, Y., Xie, Z. et al. Med-BERT: pretrained contextualized embeddings on large-scale structured electronic health records for disease prediction. npj Digit. Med. 4, 86 (2021). https://doi.org/10.1038/s41746-021-00455-y", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|37|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb37", "comment": "how is the reproducibility of the methods for the same samples? it is not share in the paper.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|37|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb37", "comment": "how can we deal with inhomogeneous deposition of the film and thus inhomogenous ageing of the thin film? in the paper the analyses on degradation are quite simple in comparison of what happens in reality (dots of degradation, coffee ring, thickness variation and thus various degradations,...)", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|37|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb37", "comment": "", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|37|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb37", "comment": "", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|37|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb37", "comment": "", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|37|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb37", "comment": "Line 78: PPV 1.7% really practically useful? If implemented in clinical practice, over 98% of interventions would be for patients who will not actually harm themselves. The statement that PPV 8.45% *minimizes* resource cost and intrusion directed at patients who will never attempt self-harm. (lines 78-79) is certainly not true as stated, though it is certainly an improvement over the (implausibly low) 1.7% baseline.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|37|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb37", "comment": "Please clarify the *meaning* of what you are predicting. ICD-10 (probably more precisely ICD-10-CM) is how the meaning is encoded, but does not fully explain what is being predicted. Are these ICD codes entered for billing purposes (what does that mean in a VA setting)? Clinical purposes (e.g., as problem list entries)? Something else? Without this information, it is hard to understand the contribution of this system beyond numerical comparison to other systems.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|37|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb37", "comment": "The VA and MIMIC populations are clinically very different (general vs ICU). It is surprising that a system pretrained on a general population performed well on a very different population. More information regarding the prediction tasks would be helpful. For example, for self-harm in PTSD, were previous ICU admissions used to predict future ICU admissions where self-harm is noted? What about patients who were discharged from ICU, had PTSD and harmed themselves but were not subsequently admitted to the same ICU?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|37|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb37", "comment": "The improvements in PPV over BERT are relatively modest in absolute terms. For example, for predicting self-harm with full history: 7.14% \\( \\\\uparrow \\) 8.67%. Is this clinically significant? E.g., how much does this practically decrease resource utilization in anticipated clinical implementation?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|37|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb37", "comment": "The prediction of pancreatic cancer ICD-10 codes one visit prior to the documentation of these codes may not be clinically useful. In other words, the system is predicting whether a human clinician is going to assign a code for pancreatic cancer on the next visit. First, billing codes are known to be poor representations of clinical reality (see comment #2 above). Second, the documentation of a code is not equivalent to the first diagnosis of the disease. Third, (even ignoring the first two points) the duration between visits may differ greatly – predicting that pancreatic cancer will be documented on the next visit in 1 year may be much more useful than if the next visit is in 1 week or 1 month. The relationship between codes and clinical reality depends on the type of visit (inpatient vs. outpatient) as well as the condition. Again, it is important to understand what the ICD-10 codes really represent in the VA system.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|37|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb37", "comment": "Line 69-70: “Such pretraining objective can leverage the clinical relations among diseases and outcomes.” Is awkward and should be rephrased.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|37|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb37", "comment": "Line 75: “…the improvements for uncommon [*ICD code predictions* or *predictions*] were substantial.”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|37|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb37", "comment": "Figure 1: What is “Exam to educational institution”?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|37|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb37", "comment": "Figure 3: “Actual disease *patient* had”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|38|Claude|1", "source": "prb", "split": "test", "paper_id": "prb38", "comment": "The paper's accuracy claims for both the band gap autocharacterization (98.5%) and degradation detection (96.9%) are based solely on comparisons to a single domain expert's manual evaluations, without any assessment of inter-rater reliability or multiple annotator consensus. This methodological weakness undermines the validity of the reported accuracy metrics because Tauc plot fitting is known to involve subjective judgment in selecting the tangent line region.\n\n\"This band gap comparison between algorithm and expert is used to determine an accuracy metric for the algorithm, assuming the expert-calculated output as ground truth.\"\nThe supplementary materials explicitly state that a single expert's evaluations serve as ground truth. This methodological approach is problematic because scientific validation of automated analysis systems should ideally involve multiple independent annotators to establish inter-rater reliability. Without such validation, it is impossible to distinguish whether discrepancies between the algorithm and the \"ground truth\" reflect algorithmic errors or inherent subjectivity in the manual fitting process. The Tauc plot method requires subjective selection of the linear region for fitting, which can vary significantly between experts.\n\"H.K. performed expert human benchmarking.\"\nThe author contributions section confirms that only a single individual (H.K.) performed the expert benchmarking that serves as ground truth for both accuracy metrics. Best practices in automated analysis validation, particularly in medical imaging and other fields requiring expert annotation, typically require multiple independent annotators with inter-rater reliability metrics such as Cohen's kappa or intraclass correlation coefficient [[1]](#citation-1). The absence of such metrics makes it impossible to assess whether the reported 98.5% accuracy reflects genuine algorithmic performance or merely the degree to which the algorithm matches one individual's subjective fitting choices.\n\"The accuracy is calculated by taking the average of a binary 0/1 for all N = 201 samples, determined based on whether or not the differences between the automatic and the expert band gap values fall within a specified energy difference threshold.\"\nThe accuracy definition further compounds the single-annotator problem. Even with perfect inter-rater agreement among experts, using a binary threshold-based accuracy metric obscures information about systematic biases or calibration errors. Moreover, without knowing the variance in expert annotations, the 0.02 eV threshold cannot be properly contextualized—it may be larger or smaller than the typical inter-expert variability.\n\nReferences:\n[1] [Inter-rater reliability was high, with an overall Cohen's Kappa of 0.924 and individual label Kappas ranging from 0.677 (apical coverage) to 0.965 (scratch)](https://www.nature.com/articles/s41598-026-35100-9_reference.pdf) - Example of inter-rater reliability assessment in image analysis validation.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|38|Claude|2", "source": "prb", "split": "test", "paper_id": "prb38", "comment": "The paper claims to present \"generalizable\" autocharacterization tools, but all experimental validation is performed exclusively on a single binary perovskite system (FA1-xMAxPbI3). Without demonstration on other material classes or compositions, the claimed generalizability remains unsupported by evidence.\n\n\"We demonstrate a generalizable composition mapping tool for high-throughput synthesized binary material systems.\"\nThe abstract explicitly claims generalizability for the composition mapping tool. However, the entire experimental validation is performed only on FA1-xMAxPbI3 perovskites. The optical properties (band gap range ~1.47-1.56 eV), degradation patterns (yellowing due to α-FAPbI3 to δ-FAPbI3 phase transition), and spectral features are specific to this material family. Without testing on other binary material systems—or even other halide perovskite compositions such as those containing Cs, Sn, Br, or Cl—the generalizability claim lacks empirical support.\n\"Currently, the autocharacterization algorithm is configured to operate only on materials with a single direct band gap.\"\nThe supplementary materials acknowledge a significant limitation: the algorithm is restricted to materials with a single direct band gap. Many semiconductor systems of practical interest have indirect band gaps (e.g., silicon), multiple band gaps, or more complex absorption edge features. This acknowledged limitation directly contradicts the broad generalizability implied in the paper's framing. Research demonstrating machine learning for materials typically validates on multiple material classes to demonstrate transferability [[2]](#citation-2).\n\"This package was made for materials printed using a High-Throughput (HT) Combinatorial Synthesis system called Archerfish (AF) built at MIT... However, this package uses various computer vision methods that allow it to be adaptible to other materials systems of different form factors. The only component of the code specific to the HT synthesis platform is the composition extraction.\"\nThe code README acknowledges the system-specific nature of the implementation. While the authors claim adaptability, they do not demonstrate it experimentally. The algorithm parameters (ev_range=[1.4, 1.65], smoothing=20, R² threshold of 0.990) appear optimized for the FA-MA perovskite system's band gap range and are hardcoded in the implementation, raising questions about performance on materials with different spectral characteristics.\n\nReferences:\n[2] [Such limited and domain-specific datasets often result in models that lack generalization capability and exhibit bias toward the material class on which they were trained](https://link.aps.org/doi/10.1103/l92g-tkds) - Discussion of generalization limitations when training on single material classes.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|38|Claude|3", "source": "prb", "split": "test", "paper_id": "prb38", "comment": "The headline accuracy metric of 98.5% for band gap autocharacterization is obtained using an energy difference threshold of 0.02 eV that appears arbitrarily selected. The paper shows accuracy depends strongly on this threshold (Figure S-6b), but does not justify why 0.02 eV is an appropriate tolerance or relate it to application requirements or measurement uncertainties.\n\n\"The algorithm achieves 98.5% accuracy within 0.02eV and as the threshold becomes tighter, the algorithm accuracy is expected to decrease.\"\nThe supplementary materials acknowledge that accuracy varies with the chosen threshold, with tighter thresholds yielding lower accuracy. However, the paper reports only the 98.5% figure prominently without adequate justification for why 0.02 eV is the appropriate threshold. For context, the total band gap variation across the FA1-xMAxPbI3 series is approximately 0.1 eV (from ~1.47 to ~1.57 eV), meaning the 0.02 eV tolerance represents 20% of the entire compositional trend. This raises questions about whether the accuracy metric reflects meaningful scientific precision or simply a sufficiently loose tolerance.\n\"Figure S-6b illustrates the accuracy of the automatic algorithm as a function of the energy difference threshold.\"\nFigure S-6b explicitly shows that accuracy drops substantially at tighter thresholds. For example, at 0.01 eV threshold, accuracy appears to drop below 90%. The practice of selecting thresholds that optimize apparent performance is a recognized concern in machine learning evaluation [[3]](#citation-3). Best practice would require either justifying the threshold based on application requirements or reporting performance across multiple thresholds with appropriate statistical treatment.\n\"The bounds of ±0.02eV are used because they empirically fit the expert-calculated pre-degradation band gaps (blue points) with little to no tolerance.\"\nThe paper acknowledges that the 0.02 eV threshold was selected empirically to fit the data, rather than being determined by application requirements or physical considerations. This post-hoc threshold selection raises concerns about overfitting the accuracy metric to the specific dataset. A rigorous evaluation would specify the acceptable tolerance a priori based on the precision required for downstream applications (e.g., device performance prediction).\n\nReferences:\n[3] [Used external image databases (reducing selection bias); very high accuracy suggests possible class imbalance or overfitting; limited clinical context reported](https://pmc.ncbi.nlm.nih.gov/articles/PMC12783025/) - Systematic review discussing threshold selection and potential overfitting in automated analysis.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|38|Claude|4", "source": "prb", "split": "test", "paper_id": "prb38", "comment": "The paper acknowledges significant batch-to-batch variability in sample morphology and reports selecting batches \"with similar morphology\" to minimize this variation. However, the impact of this variability on the autocharacterization accuracy is not quantified, raising questions about whether the reported accuracies would hold for samples with different morphological characteristics.\n\n\"Variability exists across samples manufactured using our high-throughput combinatorial printer, as the setup is designed for low-cost, scalable, and high-throughput screening rather than high-fidelity experiments.\"\nThe supplementary materials explicitly acknowledge that the high-throughput manufacturing process introduces significant sample-to-sample variability. This is an important acknowledgment, but the implications for the autocharacterization accuracy are not addressed. If the algorithm was trained/validated only on morphologically similar batches, its performance on more variable samples remains unknown.\n\"Figure S-2 shows the post-degradation structural morphology differences between two of the same sample compositions across two separate batches, manufactured using the same printing conditions.\"\nFigure S-2 demonstrates substantial morphological differences between batches (uniform vs. jagged grain boundaries). These differences affect degradation behavior and likely affect the optical properties used for band gap determination. The paper does not report how such morphological variations affect autocharacterization accuracy.\n\"In this study, three batches of samples were selected with similar morphology in an attempt to minimize this variation and maintain the emphasis of the paper on the assessment of the proposed automatic characterization methods, rather than on the method of synthesis.\"\nThe explicit selection of similar-morphology batches represents a form of selection bias that may inflate the reported accuracy metrics. For the autocharacterization tools to be practically useful in high-throughput screening applications—which inherently involve sample-to-sample variability—accuracy should be validated across morphologically diverse samples rather than only on carefully selected batches with similar characteristics.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|38|GPT|1", "source": "prb", "split": "test", "paper_id": "prb38", "comment": "This paper’s degradation-detection result (96.9% accuracy; PR-AUC 0.853) is not convincingly validated because the decision boundary for the degradation classifier is selected to maximize accuracy on the same dataset used for reporting performance, and because the “ground truth degradation” label is defined using a proxy criterion (expert-measured band-gap change beyond an empirically chosen threshold) rather than an independent degradation measurement.\n\n“This classification performance of the autocharacterization algorithm achieves a precision-recall AUC (area under the curve) of 0.853 (Supplementary Figure S-10c), and a maximal accuracy of 96.9%, relative to the ground truth (Supplementary Figure S-10d).”\nThis sentence reports a single-point “maximal accuracy” alongside PR-AUC, but it does not describe any protocol that prevents threshold selection from biasing the accuracy upward (e.g., a held-out test set, nested cross-validation, or reporting accuracy at a pre-registered decision boundary). When “maximal accuracy” is reported, it typically implies that some threshold was tuned to the dataset; if the same data are then used to evaluate the tuned threshold, the resulting accuracy is an optimistic estimate of future performance. Because the paper’s main claimed contribution includes accurate automated degradation quantification, such an evaluation leak directly affects the validity of the central quantitative claim. The issue is not cosmetic: even small threshold tuning can materially inflate accuracy in imbalanced or noisy-label settings. Without an explicitly independent evaluation, the reported 96.9% should be interpreted as an upper bound rather than a reliable estimate. The paper does not provide uncertainty bounds (e.g., confidence intervals) for PR-AUC/accuracy to quantify sensitivity to sampling variability.\n“Figure S-10d shows the effect of moving the decision boundary on the accuracy in detecting the degradation. Considering recall, precision, and accuracy, \\( I_c \\) performs optimally, with an accuracy of 96.9%, in detecting degraded samples when the decision boundary is set to \\( 0.92 \\times 10^5 \\)px-hr.”\nThis sentence makes explicit that the decision boundary is varied and that the reported accuracy corresponds to the optimum on that sweep. Selecting a threshold by maximizing accuracy is a form of model/operating-point selection and should be separated from final evaluation to avoid biased performance reporting. If the same dataset is used both to choose the “optimal” threshold and to compute the “optimal” accuracy, the accuracy is not an unbiased estimate of how the system will perform on new experiments (e.g., new degradation runs, lighting conditions, or compositions). The paper does not describe splitting the samples into calibration (threshold selection) and test subsets, nor repeating the threshold selection across folds, which would be standard to control this bias. Moreover, because the paper emphasizes scalability and deployment in high-throughput workflows, generalization across batches and future experiments is the real target; an in-sample optimized threshold does not establish that. Reporting a full PR curve is helpful, but the headline “96.9% accuracy” remains threshold-dependent and, as written, tuned.\n“To benchmark the algorithm, the difference in domain expert-computed band gaps before and after degradation is used as a ground truth to quantify whether the material has truly degraded or not.”\nThis sentence defines the label (“ground truth degradation”) using an indirect proxy derived from a separate band-gap estimation process, rather than a direct physical assay of degradation (e.g., phase fraction from XRD, chemical decomposition products, or electrical performance loss). Using band-gap change as a proxy can be reasonable in specific contexts, but it introduces label noise because band-gap estimation itself has measurement and analysis variability, and because different degradation pathways can manifest differently in band gap. The paper does not quantify uncertainty in the expert band-gap estimates or propagate that uncertainty into the degradation labels, despite using a hard threshold (±0.02 eV). That means some samples near the threshold could flip labels due to analysis noise rather than true degradation, which directly affects classifier metrics and decision boundary selection. Because the labels are derived from regression-fit residuals (see next quote), the label definition also depends on a fitted model, adding another layer of potential bias. This undermines the robustness of the reported degradation classification performance.\n“Hence, in Figure S-10(a), any expert-calculated post-degraded band gaps (red points) samples that fall outside of the ±0.02eV bounds, with respect to the regression fit line to the expert-calculated pre-degradation band gaps (blue points), are considered to exhibit “Ground Truth Degradation”.”\nThis sentence shows that the label is not simply a direct pre/post comparison per sample, but is defined relative to a regression line fitted to pre-degradation band gaps, with an “empirically” chosen ±0.02 eV band. That makes the ground truth definition model-dependent: different fits (or different subsets) could change which points fall outside the band, especially if there are heteroskedastic errors across composition. The method also implicitly assumes that the regression residual distribution of pre-degradation band gaps is the correct basis to set the degradation threshold, but no justification is given for using that same tolerance for post-degradation classification. In addition, the supplementary explicitly notes a “break in the graph” because “compositions had no band gap after degradation, reported as 0.0eV” (Figure S-10a caption), which suggests that missing/failed band-gap measurements are being folded into the labeling scheme in a way that could strongly influence the classifier evaluation. Without a clearer treatment of missingness and uncertainty, the “ground truth degradation” labels may not be reliable enough to support the strong conclusions. This is particularly important because the reported degradation mechanism is visually described as yellowing/phase transition, which may not map one-to-one to band-gap shifts.\n“In contrast, in supervised machine learning tasks, where the goal is prediction, it is standard practice to split the data into training and test sets for model development and evaluation, respectively …” ([4](https://arxiv.org/html/2206.11721v2))\nThe paper’s degradation classifier involves choosing an operating point (“decision boundary”) and then reporting performance metrics; this is conceptually a predictive modeling workflow even if the “model” is a single scalar metric \\(I_c\\). The quoted statement summarizes standard practice: separate model/threshold selection from evaluation to obtain an unbiased estimate of generalization. The paper instead reports the maximal accuracy across thresholds, which corresponds to choosing the threshold using the evaluation data. This mismatch with common evaluation practice matters because the paper’s primary contribution is claimed accuracy and throughput of automated characterization, not just a qualitative trend. Even if a full train/test split is not feasible due to limited sample count, the paper could have used cross-validation or reported confidence intervals; it does not. Therefore, the reported accuracy should be treated with caution.\n“It usually divides a training dataset further into training and validation subsets, for example for cross-validation …” ([1](https://journals.plos.org/plosone/article?id=10.1371/journal.pone.0118432))\nWhile this paper is not training a conventional classifier, it does perform model selection in the form of choosing an \\(I_c\\) threshold (“decision boundary”) that is declared optimal because it maximizes accuracy. The quoted statement highlights the standard separation between model selection (including threshold selection) and final evaluation via validation/test data. If the “optimal” operating point is selected using the same dataset on which accuracy is reported, performance estimates are biased upward and do not reliably predict future behavior. This concern is particularly acute when class imbalance exists (as the authors state), because accuracy can vary materially with the operating point while remaining visually plausible. The paper does not document any procedure that guards against this leakage (e.g., selecting the threshold on one batch and evaluating on another). Consequently, the reported 96.9% accuracy is not robustly supported by the described evaluation protocol.\n“However, environmental factors such as moisture, oxygen, heat, and light exposure further accelerate degradation, exacerbating operational stability issues…” ([3](https://hal.science/hal-05377984v1/file/eScience_2025.pdf))\nThis statement from the perovskite stability literature underscores that “degradation” is multi-causal and can proceed through multiple environmental pathways, which may not all map cleanly to a single proxy observable like band-gap shift beyond a fixed tolerance. In the reviewed paper, the ground-truth label is based on band-gap deviation relative to a fitted baseline, which may miss degradations that primarily manifest through other mechanisms or that change device-relevant properties without producing a large band-gap shift. Because the proposed degradation detector is trained/evaluated against this proxy label, any mismatch between the proxy and true degradation mechanisms directly limits the validity of the reported accuracy as a measure of real degradation detection. This matters for the paper’s conclusions because the method is positioned as a general “stability measurement” tool in high-throughput workflows. A stronger evaluation would triangulate degradation labels using independent physical assays (e.g., phase fraction by XRD, chemical decomposition markers, or electrical performance metrics), or at minimum quantify label uncertainty. Without such validation, the reported classifier performance may not transfer beyond the specific degradation mode and conditions studied.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|38|GPT|2", "source": "prb", "split": "test", "paper_id": "prb38", "comment": "This paper’s validation of automated band-gap estimation is not methodologically sufficient because it reduces continuous band-gap errors to a thresholded 0/1 “accuracy” against a single expert’s manual fit, while simultaneously acknowledging systematic underprediction and not reporting uncertainty or error distributions that would be needed to support the claimed precision and reliability.\n\n“The accuracy is calculated by taking the average of a binary 0/1 for all \\( N = 201 \\) samples, determined based on whether or not the differences between the automatic and the expert band gap values fall within a specified energy difference threshold (shown along the x-axis of Figure S-6b).”\nThis sentence defines the core metric used to claim quantitative performance for band-gap estimation, and it is a thresholded classification-style metric rather than a regression error metric. A 0/1 threshold collapses information about error magnitude, so it cannot distinguish systematic bias from small random errors, nor can it reveal whether errors are concentrated in particular composition ranges (e.g., near phase boundaries). Because the automated method is a regression/estimation procedure producing a real-valued band gap, common practice would be to report at least MAE/RMSE (and often bias and calibration curves) along with distributions of residuals. The paper also does not describe how sensitive the reported “accuracy” is to the chosen threshold, except by plotting it as a function of threshold; that does not substitute for reporting the actual error distribution. Treating a single expert’s manual fit as “ground truth” also ignores inter-annotator variability and the known subjectivity of selecting linear Tauc regions, so the binary metric can be driven by labeling noise. Overall, this definition makes the headline “98.5% accuracy” hard to interpret as a measurement claim.\n“This band gap comparison between algorithm and expert is used to determine an accuracy metric for the algorithm, assuming the expert-calculated output as ground truth.”\nThis sentence makes explicit that the evaluation assumes a single expert’s manual outputs are ground truth, but it does not provide evidence that expert variability is negligible relative to the stated tolerance (±0.02 eV). In many optical band-gap workflows, different reasonable choices of linear fitting interval, smoothing, and baseline can lead to nontrivial differences in extracted \\(E_g\\), which means “ground truth” is not directly observable without specifying a protocol and uncertainty. The paper does not report repeated expert fits, inter-rater agreement, or uncertainty estimates for the expert’s numbers. As a result, some fraction of automated-vs-expert differences within or outside the threshold could reflect annotation noise rather than algorithmic performance. This is especially relevant because the paper leverages the expert band-gap differences again as ground truth for degradation labeling, compounding the impact of this assumption. Without quantifying expert uncertainty, the reported performance may be overstated.\n“The autocharacterization output achieves a strong linear fit of \\( R^2 = 0.975 \\) with the expert-calculated results, however, a systematic underprediction of the autocharacterization algorithm is noted. Relative to the expert-computed band gap, the autocharacterization method achieves 98.5% accuracy within a 0.02eV range …”\nThis sentence acknowledges systematic underprediction, which is a substantive error mode (bias) that should be quantified and, ideally, corrected or at least characterized as a function of composition or band-gap value. Reporting \\(R^2\\) alongside a within-tolerance “accuracy” does not resolve whether the estimator is calibrated: a biased estimator can still have high \\(R^2\\) if it is monotonic. If the goal is automated property estimation for materials discovery, bias can meaningfully distort derived composition–property trends and downstream optimization decisions. The paper does not report whether the systematic underprediction is constant, linear, or nonlinear, nor does it report a post-hoc calibration step or uncertainty bands on predictions. Moreover, the use of a fixed ±0.02 eV tolerance is not justified via measurement uncertainty; it is treated as an empirical threshold. This undermines the strength of the conclusion that the algorithm is “accurate” in a metrologically meaningful sense.\n“When reporting the result of a measurement of a physical quantity, it is obligatory that some quantitative indication of the quality of the result be given so that those who use it can assess its reliability.” ([2](https://www.bipm.org/documents/20126/2071204/JCGM_100_2008_E.pdf))\nThe paper’s core claims are framed as quantitative measurement/characterization (band gaps and degradation), so the reporting standards around measurement quality and uncertainty are directly relevant. While the paper reports thresholded “accuracy,” it does not provide uncertainty estimates on the automated band gaps themselves (e.g., per-sample uncertainty from spectral noise, segmentation variability, and fit choice), nor does it provide uncertainty on summary metrics across batches. Without uncertainty quantification, it is difficult to assess whether a ±0.02 eV window represents a meaningful tolerance relative to experimental variability. The JCGM guidance highlights that reliability assessment requires quantitative quality indicators tied to measurement dispersion, not only point estimates. In this paper, a single “accuracy within threshold” number cannot substitute for uncertainty reporting because it hides both bias and heterogeneity in errors. This omission also makes it hard to compare the method fairly to alternative approaches in the literature.\n```python\nR_tol = 0.990  # R^2 linear regression fit tolerance for line segments\n...\npeaks = scipy.signal.find_peaks(tauc_smooth.iloc[:, i + 1], height=200,\n                                width=(0, 999999))\n```\nThese code lines show that the algorithm includes hard-coded thresholds (e.g., \\(R^2\\ge 0.990\\) for recursive segmentation; peak “height=200” for peak finding) that can materially affect which linear regions and peaks are selected for the final Tauc fit. When such thresholds are used, performance should be reported in a way that reveals sensitivity to parameter choices and data conditions (noise levels, intensity scaling, composition-dependent spectral changes). A single thresholded agreement metric (within ±0.02 eV) does not reveal robustness to these design choices. The paper also does not provide an ablation or sensitivity analysis for these parameters, despite claiming generalizability. Because the code structure suggests several implicit hyperparameters, the evaluation should quantify uncertainty or variability across reasonable parameter ranges or across repeated runs. Without that, the conclusions about accuracy are less robust. This is especially important given the paper’s stated observation of systematic underprediction.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|38|GPT|3", "source": "prb", "split": "test", "paper_id": "prb38", "comment": "The paper’s reproducibility is materially weakened because it claims “complete working examples” and a one-command example workflow, but the provided example execution fails under dependency versions permitted by the published requirements, and the code uses OS-specific path handling that can break cross-platform execution.\n\n“All code used to develop the autocharacterization and computer vision algorithms are available publicly with complete working examples.”\nThis sentence sets an expectation that an independent reader can run the provided code to reproduce the pipeline behavior (at least on example data) without substantial debugging. Reproducibility claims are part of the paper’s scientific contribution because the work is presented as an automated, scalable workflow intended for adoption. When the public code does not run as described, it prevents verification of reported throughputs, preprocessing steps, and algorithmic details beyond the paper’s narrative. This can also prevent downstream users from validating whether the algorithm behaves similarly on their own data. The claim is therefore falsifiable via execution of the examples, and the burden is on the authors to ensure that the examples run under the stated environment. In this case, the dependency specification is permissive (“>=”), so incompatibilities within that range are a direct reproducibility risk. The issue is amplified because the pipeline includes multiple stages (download, segmentation, plotting, saving outputs) where failures can occur.\n“A quicker demonstration can be obtained by using the main.py file. The user only needs to run the file and the example data will be automatically analysed.”\nThis statement indicates that `main.py` is the primary reproducible entrypoint and that it should run end-to-end on provided example data. This kind of “single-command” claim is important because it is the simplest way for readers to verify the method and for reviewers to reproduce the reported results. In practice, however, the script execution fails before completing the pipeline due to plotting code that does not specify a target Axes for the colorbar (see below). Because the failure occurs in a central module (`vision.segmentation`), it blocks the rest of the workflow and prevents users from obtaining the outputs promised in the README (e.g., extracted spectra, segmented results, band-gap plots). The failure also indicates that the provided requirements are insufficiently pinned/validated against the code. This undermines the paper’s reproducibility claims in a concrete, user-facing way.\n```text\nmatplotlib >= 3.5.3\n```\nThe dependency constraint allows installation of modern Matplotlib releases (including 3.10.x) while still satisfying the published requirements. Therefore, if the code fails on such versions, the problem is not an “unsupported environment” edge case but a mismatch between the declared dependency range and actual compatibility. Reproducible research code typically pins exact versions (or provides a lockfile/conda environment) when behavior depends on library APIs, especially for plotting and I/O. Here, the requirements’ permissive bounds shift the burden of compatibility onto the reader, contrary to the paper’s claim of complete working examples. In addition, the paper’s empirical claims about throughput (minutes for hundreds of samples) are inseparable from the implementation details, so an inability to run the implementation blocks verification. This is a substantial reproducibility flaw rather than a minor packaging detail. The failure mode is deterministic and occurs before any user customization of parameters.\n```python\nfig, ax = plt.subplots(figsize=(8, 4))\n...\nfig.colorbar(mpl.cm.ScalarMappable(norm=mpl.colors.Normalize(vmin=0, vmax=100), cmap=mpl.cm.viridis), label='%MA')\n```\nThis code calls `Figure.colorbar` without providing `ax=` or `cax=` and without attaching the `ScalarMappable` to an Axes, which can fail on modern Matplotlib versions. Because this call sits inside the segmentation routine, the core example workflow breaks even after successfully downloading the example data, making the “quick start” unreproducible. The code also uses `plt.show()` unconditionally in the segmentation function, which can further block execution in non-interactive or headless environments common for reproducibility and CI. These are not merely stylistic issues: they cause runtime exceptions (see below) and prevent the production of any downstream results. The problem is also easy to trigger because it is on the default path of `main.py`. This directly contradicts the “complete working examples” claim.\n“The one or more parent Axes from which space for a new colorbar Axes will be stolen. This parameter is only used if *cax* is not set.” ([5](https://matplotlib.org/stable/api/_as_gen/matplotlib.figure.Figure.colorbar.html))\nThe Matplotlib documentation clarifies that when `cax` is not provided, the function relies on knowing which parent `ax` to “steal space” from. In the reviewed code, no `ax` is passed and the mappable is not associated with a plotted artist on an Axes, so Matplotlib cannot infer which Axes should be used. This directly explains why execution can raise “Unable to determine Axes to steal space for Colorbar” under current Matplotlib behavior. Because the paper’s requirements explicitly allow current Matplotlib versions, following the documented API is essential for reproducible execution across environments. The documentation even provides an example using `fig.colorbar(..., ax=ax)`, which the code omits. This is therefore a straightforward API misuse that undermines reproducibility. In scientific software intended for broad use, such plotting code should either be robust or optional.\n```text\nTraceback (most recent call last):\n  File \".../preprint/code/main.py\", line 45, in <module>\n    data, sgmnt = vision.segmentation(...)\n  File \".../preprint/code/vision.py\", line 92, in segmentation\n    fig.colorbar(...)\nValueError: Unable to determine Axes to steal space for Colorbar. Either provide the *cax* argument to use as the Axes for the Colorbar, provide the *ax* argument to steal space from it, or add *mappable* to an Axes.\n```\nThis stack trace demonstrates that, when running the advertised `main.py` entrypoint on the provided example data, execution fails with a Matplotlib `ValueError`. Because the error is raised during the core segmentation step, it prevents any subsequent steps from running (band-gap extraction, saving outputs, and any of the reported runtime measurements). The error message itself explicitly indicates what is missing (an Axes to attach the colorbar to), corroborating that the failure is due to code/API incompatibility rather than missing data. Since the dependency specification allows Matplotlib versions that enforce this behavior, the example is not reproducible “as provided.” A reader attempting to reproduce the results would need to manually patch the code or downgrade Matplotlib, neither of which is described in the paper or README. This is a substantial barrier to reproducibility.\n```python\nplt.savefig(f'{savepath}\\\\{current_tauc}.png', dpi=300, bbox_inches='tight')\nEG.to_csv(f'{savepath}\\\\Extracted_Band_Gaps.csv')\n```\nThese lines show hard-coded Windows-style path separators (`\\\\`) used to build output file paths. On POSIX systems (Linux/macOS), backslashes are valid filename characters rather than directory separators, which can lead to unexpected output locations or filenames and can break downstream scripts that assume standard paths. Cross-platform path handling is a core reproducibility requirement for computational papers with public code, especially when the paper positions the tool as broadly usable in high-throughput workflows. This issue compounds the Matplotlib runtime failure by making file outputs less predictable even when execution proceeds. The problem could be avoided by using `os.path.join` or `pathlib`, but as written it creates platform-specific behavior. Because the paper does not constrain the OS environment or provide a container, this is a reproducibility gap. Together with the failing example entrypoint, it undermines the claim that the release includes “complete working examples.”", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|38|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb38", "comment": "The paper's composition mapping methodology is flawed because it calculates the composition of deposited droplets based on instantaneous pump speeds without accounting for the hydraulic delay (dead volume) between the pumps and the deposition nozzle.\n\n\"Thus, to determine the composition of each material deposit, \\( \\omega_{\\text{FA}} \\) and \\( \\omega_{\\text{MA}} \\) are spatially and temporally mapped onto the computer vision-segmented samples, \\( (\\tilde{X}, \\tilde{Y})_n \\in N \\), and then integrated over time to determine each sample’s computed FA$_{1-x}$MA$_x$PbI$_3$ composition: \\[ x(t) \\approx \\int_{t_a}^{t_b} \\frac{\\omega_{\\text{MA}}(t)}{(\\omega_{\\text{MA}}(t) + \\omega_{\\text{FA}}(t))} dt, \\]\"\nThis equation assumes that the composition deposited at time $t$ corresponds exactly to the pump speeds at time $t$. However, in any fluidic system with a mixing chamber and tubing, there is a physical distance between the pumps and the nozzle, resulting in a time delay (lag) between the pump action and the deposition of the corresponding mixture.\n\"A pinch valve breaks up the fluid flow within a 1/32”ID × 3/32”OD silicone tube, actuating at 11Hz frequency and 5% duty cycle to deposit each sample as a discrete droplet onto the cleaned glass slide.\"\nThe presence of tubing and a mixing chamber (\"enter a mixing chamber prior to deposition\") confirms the existence of a dead volume. The manuscript and Supplementary Information do not describe any calibration step to measure or correct for this delay.\n\"motor_coords = pd.merge(df_motors, df_coords, on='time', how='inner')\"\nIn the provided code `compextractorb.py`, the motor speed data and the printer gcode coordinates are merged directly on the `time` column without applying any time-shift or lag correction. This implies that the code assumes zero delay, which is physically impossible.\n\"Long reaction times, in contrast, required lengthy microchannels (35) that resulted in larger dead volumes and high back pressures that could destabilize\" [1]\nAs noted in other literature on automated synthesis, dead volumes are a critical factor that can distort composition gradients if not properly accounted for. By neglecting this, the \"ultra-high resolution\" composition axis presented in the paper is likely distorted, shifting the assigned composition values relative to the true values.\n\nReferences:\n[1] R. W. Epps et al., \"Automated Nanocrystal Synthesis: Lessons from 25 Years of Microfluidic Reactors,\" *Nano Letters*, vol. 17, no. 11, 2017. https://pubs.acs.org/doi/10.1021/acs.nanolett.5c05228", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|38|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb38", "comment": "The proposed \"autocharacterization\" algorithm for band gap extraction relies on a heuristic recursive segmentation method with fixed parameters, which lacks the robustness required for a generalizable tool and may fail on data with noise or complex spectral features.\n\n\"recursively segmenting the Tauc curves into linear segments (\\( R^2 \\geq 0.990 \\)) to find the regression line of best fit between peaks\"\nThe algorithm relies on a hard-coded determination coefficient threshold ($R^2 \\geq 0.990$) to identify \"linear\" regions. This heuristic is brittle; noisy data might fail to meet this threshold, or non-linear regions might accidentally meet it over short segments.\n\"model = LinearRegression().fit(np.vstack([X_tol_sort[-1 - e], X_tol_sort[-2 - e]]), np.vstack([Y_tol_sort[-1 - e], Y_tol_sort[-2 - e]]))\"\nIn `bandextractor.py`, the code forces a linear fit to the union of two adjacent segments found by the recursive splitter. This assumes that the linear region of the Tauc plot always spans exactly two segments of the split. If the linear region is captured by a single segment or requires more than two, this hard-coded logic will produce an incorrect fit.\n\"Escobedo *et al.* [25] develop automated programs to compute the band gap of semiconductor materials, however, the throughput of the software is insufficient\"\nThe authors criticize existing methods [2] primarily on throughput. However, established methods often use more robust fitting routines (e.g., fitting the full absorption edge equation) rather than simple linear segmentation. The proposed method trades robustness for speed without demonstrating that it maintains accuracy on difficult cases (e.g., multiphase samples or indirect tails).\n\nReferences:\n[2] A. Escobedo-Morales et al., \"Automated method for the determination of the band gap energy of pure and mixed powder samples using diffuse reflectance spectroscopy,\" *Heliyon*, vol. 5, e01505, 2019. https://doi.org/10.1016/j.heliyon.2019.e01505", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|38|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb38", "comment": "The paper claims to provide a generalizable \"autocharacterization\" tool for degradation, but the developed method relies solely on a color-change metric that is specific to the $\\alpha$-to-$\\delta$ phase transition in the studied perovskite system and may not be applicable to other degradation pathways.\n\n\"autonomously compute the degree of degradation in 200 unique compositions... generating ultra-high compositional resolution trends of band gap and stability.\"\nThe claim implies a general capability to detect degradation. However, the method defines degradation intensity ($I_c$) as a color distance in CIELAB space.\n\"The yellowing pattern of the FA-rich samples is shown in Figure 7b as a result of the phase change from favorable cubic phase \\( \\alpha \\)-FAPbI\\(_3\\) to the non-perovskite hexagonal phase \\( \\delta \\)-FAPbI\\(_3\\)\"\nThe validation is performed on a system where degradation is known to cause a distinct color change (black to yellow).\n\"Understanding the stability of mixed a-cation lead iodide perovskites.\" [3]\nLiterature shows that perovskite degradation can involve various pathways, some of which (e.g., hydration or decomposition to PbI2) might have different optical signatures or might not result in a monotonic \"yellowing\" that correlates linearly with the $I_c$ metric. By framing the tool as a general \"degradation detector\" without specifying its limitation to color-changing phase transitions, the paper overstates the tool's applicability.\n\nReferences:\n[3] B. Charles et al., \"Understanding the stability of mixed A-cation lead iodide perovskites,\" *Journal of Materials Chemistry A*, vol. 5, pp. 22495–22499, 2017. https://doi.org/10.1039/C7TA08617A", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|38|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb38", "comment": "The manuscript evaluates the performance of the proposed tools primarily by comparing them to manual characterization, ignoring the existence of other automated high-throughput characterization systems in the field, which creates a misleading impression of the advancement.\n\n\"most sample characterization methods are either slow (conventional rates of \\(10^1\\) samples per hour, approximately 1000x slower) or rigid\"\nThe authors set up a \"strawman\" comparison against manual methods ($10^1$ samples/hr).\n\"Similarly, Langner et al. [10] and Wang et al. [9] develop significantly higher throughput drop casting tools... however, their characterization measurements are also fixed\"\nThe authors dismiss existing automated systems [4, 5] as \"rigid\" or \"fixed\". However, these systems also achieve high throughputs. A fair comparison would be against these automated systems in terms of throughput, accuracy, and flexibility, rather than claiming an \"85x speedup\" against a manual process that is rarely used in high-throughput campaigns.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|38|Gemini|5", "source": "prb", "split": "test", "paper_id": "prb38", "comment": "The \"generalizable\" software tools provided are heavily hard-coded to the specific log formats and hardware configuration of the authors' custom printer, limiting their utility as open-source community tools.\n\n\"data_split = motor_speeds.split('_')... i = d.split('T')[1].split('A')...\"\nIn `compextractorb.py`, the data parsing logic is hard-coded to a specific string format generated by the authors' microcontroller.\n\"gcode['sum'] = gcode.iloc[:, 0] + gcode.iloc[:, 1]\"\nThe composition mapping relies on parsing a specific G-code structure. Users with different printers or motion controllers would need to completely rewrite the data ingestion layer. While \"code availability\" is claimed, the code is more of a specific analysis script for this one experiment than a generalizable \"tool\" or \"library\" as implied by the title \"Autocharacterization\".\n\nReferences:\n[1] R. W. Epps et al., \"Automated Nanocrystal Synthesis: Lessons from 25 Years of Microfluidic Reactors,\" *Nano Letters*, vol. 17, no. 11, 2017. https://pubs.acs.org/doi/10.1021/acs.nanolett.5c05228", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|38|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb38", "comment": "[Introduction] The introduction has been written in a rather verbose fashion. It made it difficult to follow in parts. A partial rewrite is needed here if a broad audience is to be served. The phrasing could be more concise e.g. \\\"The importance of developing rapid and accurate methods of characterization for HT materials discovery and optimization derives from the intractable nature of exhaustively testing every material within a functional material’s search space using these conventional tools [14].\\\" Also, in the above quote, I believe 'intractable' is used incorrectly.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|38|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb38", "comment": "[Introduction] The authors state: \\\"For one to exhaustively search this subspace at 1% compositional steps would require synthesizing and characterizing \\(7 \\times 10^{12}\\) unique material samples (Supplementary Figure S-14).”\\n\\nAnd then state: “Thus, only small regions of this search space can be explored experimentally with current methods, given the large discrepancy between search space size and characterization throughput”\\n\\nThe above isn’t strictly true, given the large number of unique materials one could either look at small regions of a search space or sparsely look at many regions.\\n\\nThe selection of papers displaying the current state of the art is commendable and are good example of holes in the art in producing automated processes for analyzing band gaps. However, the aims of the authors’ current work seem somewhat lost in this. They state that only small regions of the search space can be explored, then give examples of bottlenecks in analysis.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|38|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb38", "comment": "[Results] One point that would improve the statistical analysis would be to ensure the reader that the regression analysis is being performed on data for which regression is applicable, i.e. show that the data are not fat-tailed.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Claude|1", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "The paper reports benchmark performance metrics as single point estimates without standard deviations, confidence intervals, or statistical tests, despite the inherently stochastic nature of LLM outputs and despite the methodology section indicating each task was evaluated multiple times. This undermines the reliability and interpretability of the claimed performance differences between GPT-4o and GPT-3.5-turbo-0125.\n\n\"GPT-4o exhibits exceptional proficiency in documentation-centric operations, achieving a 92% success rate, complemented by robust execution in analysis (71%) and computational tasks (70%).\"\nThe paper reports precise percentages (92%, 71%, 70%) without any measure of variance or uncertainty. Given that LLM outputs are inherently stochastic, and that the code repository shows each task was run 3 times, these percentages should be accompanied by standard deviations or confidence intervals. Without uncertainty estimates, readers cannot assess whether the reported differences between models are statistically significant or simply within the range of random variation. This is particularly problematic for making claims about model superiority.\n\"To ensure robustness, we manually evaluated all questions using GPT-4o and GPT-3.5-turbo-0125, verifying the output log files and AFM software results multiple times in collaboration with different researchers to eliminate potential human errors.\"\nWhile the methodology mentions \"multiple times\" evaluation, there is no quantification of variance across these runs in the reported results. The JSON data files in the code repository (e.g., question_1.json) contain three separate evaluation results for each task, but the paper does not aggregate these with proper statistical measures. Best practices in LLM evaluation recommend reporting uncertainty through credible intervals or standard deviations across runs to enable meaningful model comparison.\n\"Pass@$k$ is widely used to report performance for LLM reasoning, but it often yields unstable, misleading rankings, especially when the number of trials (samples) is limited and compute is constrained. We present a principled Bayesian evaluation framework that replaces Pass@$k$ and average accuracy over $N$ trials (avg@$N$) with posterior estimates of a model's underlying success probability and credible intervals, yielding stable rankings and a transparent decision rule for differences.\" [[1]](#citation-1)\nThis recent work on LLM evaluation methodology (ICLR 2026) explicitly recommends uncertainty quantification through Bayesian credible intervals rather than point estimates. The AILA paper's lack of uncertainty measures contradicts emerging best practices in the LLM evaluation literature. The paper makes comparative claims (e.g., \"80% versus 0% success\") that would benefit significantly from proper statistical treatment to determine whether observed differences are meaningful.\n\nReferences:\n[1] [Don't Pass@k: A Bayesian Framework for Large Language Model Evaluation](https://openreview.net/forum?id=PTXi3Ef4sT) - ICLR 2026 Conference Submission", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Claude|2", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "The benchmark evaluation is limited to only two models (GPT-4o and GPT-3.5-turbo-0125) from a single provider (OpenAI), despite the stated goal of establishing benchmarking standards for autonomous laboratories. This severely limits the generalizability of findings regarding LLM capabilities for self-driving laboratory applications.\n\n\"Systematic evaluation of AILA using two advanced closed source language models—GPT-4o and GPT-3.5-turbo-0125—unveils distinctive execution patterns and operational efficacies.\"\nThe benchmark claims to evaluate AI agents for autonomous microscopy but only tests two models from the same provider. The code repository contains folders for additional models (Claude-3.5-sonnet, Llama-3.3-70B-versatile) indicating these were tested but not reported. This selective reporting raises questions about why these results were excluded and whether they might contradict the paper's conclusions.\n\"To enhance large language models (LLMs) for chemistry problem solving, several LLM-based agents augmented with tools have been proposed, such as ChemCrow and Coscientist. Our error analysis with a chemistry expert suggests that: For specialized chemistry tasks, such as synthesis prediction, we should augment agents with specialized tools; however, for general chemistry questions like those in exams, agents' ability to reason correctly with chemistry knowledge matters more, and tool augmentation does not always help.\" [[2]](#citation-2)\nRelated work on LLM-based scientific agents (ChemCrow, Coscientist) typically evaluates multiple model families to establish general conclusions about agent capabilities. The AILA paper's restriction to OpenAI models prevents conclusions about whether observed behaviors (e.g., the \"sleepwalking\" phenomenon) are model-specific or generalizable to other LLM architectures. This limitation is particularly important given that different model families may exhibit fundamentally different instruction-following behaviors.\n\"We present the first systematic evaluation of instruction compliance across 13 major LLMs using real-world enterprise scenarios.\" [[3]](#citation-3)\nContemporary benchmarking studies in the LLM field typically evaluate a diverse set of models (this paper evaluates 13 models across 8 families) to establish generalizable conclusions. The AILA paper's two-model comparison falls short of this standard, limiting the scientific value of its benchmarking contribution and preventing meaningful conclusions about LLM capabilities for laboratory automation across the broader landscape of available models.\n\nReferences:\n[2] [Tooling or Not Tooling? The Impact of Tools on Language Agents](https://pmc.ncbi.nlm.nih.gov/articles/PMC12765490/) - PMC 2025\n[3] [The Instruction Gap: LLMs get lost in Following Instruction](https://arxiv.org/html/2601.03269v1) - arXiv 2025", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Claude|3", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "Analysis of the released AFMBench dataset reveals that only 43% of the 100 benchmark tasks contain actual evaluation results, with 57% marked as \"NaN\" (missing data). This incomplete dataset undermines the reproducibility of the reported metrics and raises questions about the reliability of the benchmark's conclusions.\n\n\"AFMBench comprises 100 expertly curated experimental tasks (see S3.1 in Supplementary Information for a few examples of tasks; all the tasks are available in the GitHub repo) manually designed to rigorously evaluate autonomous AFM operations across multiple dimensions of complexity.\"\nThe paper claims 100 curated tasks, but verification of the released data (code/Data/afm_qs/*.json) shows that only 43 questions have actual results recorded for both GPT-4o and GPT-3.5, with 57 questions containing \"NaN\" values for both models. The script verification_code_claude-opus-4-5-20251101/check_benchmark_data.py confirms: \"Total questions: 100; GPT-4o complete results: 43; GPT-4o NaN results: 57\". This means the reported performance metrics are derived from less than half of the claimed benchmark.\n\"All the tasks in AFMBench, along with the complete log files of the responses for each of the tasks from GPT-4o and GPT-3.5 are available at: https://github.com/M3RG-IITD/AILA\"\nThe claim of \"all the tasks\" being available is misleading since the majority of tasks lack evaluation results. For example, question_50.json, question_51.json, and question_73.json all show \"result\": [{\"GPT-4\": \"NaN\", \"GPT-3.5\": \"NaN\"}]. Without complete data, the reported accuracy percentages (92% for documentation, 71% for analysis) cannot be independently verified or reproduced by other researchers.\n\"Analysis of the task architecture reveals distinct patterns in resource utilization and operational complexity. In Figure 2A, tool coordination requirements highlight a systematic preference for sophisticated workflows, with 69% of tasks demanding multi-tool integration, while 31% operate through single-tool protocols.\"\nThese architectural statistics describe the design of all 100 tasks, but the actual performance evaluation appears to be based on only 43 completed tasks. It remains unclear whether the evaluated subset is representative of the full benchmark distribution across complexity levels and task types, potentially biasing the reported performance metrics toward easier or more tractable tasks.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Claude|4", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "The paper introduces the term \"sleepwalking\" as a novel phenomenon where LLM agents perform unauthorized actions, claiming it is \"reported for the first time to the best of the authors' knowledge.\" However, this claim is based on only 3 instances from GPT-4o's instruction adherence errors, which represents an insufficient sample size to establish a new phenomenon and distinguish it from well-documented instruction-following failures in the LLM literature.\n\n\"A critical finding emerged regarding GPT4o's instruction adherence. In one of the three recorded errors, GPT-4o exceeded its designated operational limits, performing actions that were not authorized by the provided guidelines.\"\nThe \"sleepwalking\" phenomenon is based on just 3 error cases from GPT-4o, which represents 15% of GPT-4o's total 20% error rate (i.e., approximately 3 cases out of 100 tasks). Claiming to identify a new phenomenon from such a small sample is statistically problematic. The described behavior—LLMs performing additional actions beyond instructions—is consistent with well-documented instruction-following failures rather than a distinct phenomenon requiring new terminology.\n\"Similar to the observation of 'hallucination' in LLMs, these results present a unique challenge—SDLs tend to take arbitrary actions potentially based on memory rather than following the instructions, referred to hereafter as 'sleepwalking'. These issues are especially critical in sensitive experimental settings...\"\nThe proposed distinction between \"sleepwalking\" and existing concepts like hallucination or instruction non-compliance is not clearly established. The paper speculates that actions are \"potentially based on memory\" without providing mechanistic evidence. The LLM evaluation literature has extensively documented instruction-following failures including \"procedural violations\" and \"deviations from specified response patterns\" as general LLM limitations rather than phenomena specific to laboratory contexts.\n\"This phenomenon, which we term the 'instruction gap,' represents a fundamental barrier to reliable LLM deployment in production systems. [...] Our findings reveal the 'instruction gap' - a fundamental challenge where models excel at general tasks but struggle with precise instruction adherence required for enterprise deployment.\" [[3]](#citation-3)\nRecent work characterizes LLM instruction-following failures as a well-documented \"instruction gap\" phenomenon across multiple model families and domains. The behaviors described as \"sleepwalking\" in the AILA paper—performing actions beyond instructions, deviating from specified protocols—align with documented patterns of instruction compliance failures in enterprise RAG systems. Introducing new terminology for what appears to be an established phenomenon, based on only 3 observations, risks fragmenting the literature unnecessarily.\n\nReferences:\n[3] [The Instruction Gap: LLMs get lost in Following Instruction](https://arxiv.org/html/2601.03269v1) - arXiv 2025", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Claude|5", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "The benchmark employs a binary correct/incorrect classification scheme for evaluation that oversimplifies the assessment of complex experimental tasks, preventing nuanced understanding of partial successes, near-misses, and the degree to which errors affect experimental outcomes.\n\n\"To assess the evaluation of questions in terms of accuracy, we classified the answers provided by AILA into two categories: fully correct answers and incorrect or partially correct answers. A fully correct answer was considered accurate, while any incorrect or incomplete response was deemed incorrect.\"\nThe binary classification system collapses important distinctions between different types and severities of errors. A task where the agent correctly sets 4 out of 5 parameters would be scored identically to a task where it fails completely. This binary approach is particularly problematic for multi-step experimental tasks where partial completion may still provide scientific value. Modern LLM evaluation frameworks increasingly adopt graded scoring rubrics to capture performance nuances.\n\"We present a principled Bayesian evaluation framework [...] giving closed-form expressions for the posterior mean and uncertainty of any weighted rubric and enabling the use of prior evidence when appropriate. [...] The framework [...] naturally extends to graded, rubric-based evaluations.\" [[1]](#citation-1)\nContemporary LLM evaluation methodology recommends graded, rubric-based assessments that can capture partial correctness and varying degrees of task completion. The binary scoring in AFMBench prevents meaningful analysis of where and how LLMs succeed or fail within complex multi-step experimental workflows, limiting the diagnostic value of the benchmark for identifying specific areas for improvement.\n\"Evaluation outcomes are modeled as categorical (not just 0/1) with a Dirichlet prior.\"\nBest practices in LLM benchmarking, as evidenced by recent methodological work, recognize that categorical or continuous evaluation outcomes better capture the complexity of task performance than binary measures. For AFM operations involving multiple parameters and sequential steps, a graded evaluation would provide more actionable insights for framework development.\n\nReferences:\n[1] [Don't Pass@k: A Bayesian Framework for Large Language Model Evaluation](https://openreview.net/forum?id=PTXi3Ef4sT) - ICLR 2026 Conference Submission", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|GPT|1", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "The paper’s AFMBench “efficiency” metric is not a valid measure of experimental efficiency because it excludes AFM scan time and excludes time for incorrect answers, yet the paper uses the resulting numbers to support claims about time savings in real experiments.\n\n“To ensure precise efficiency measurements, scanning time for images and the time taken by questions with incorrect answers were excluded from the analysis.”\nExcluding scan time removes a central part of AFM experiment duration and breaks any end-to-end interpretation of efficiency. Excluding time for incorrect answers introduces survivorship bias by omitting recovery and rework costs that drive real throughput. These choices can make a less reliable agent appear faster by discarding slow failures and retries from the timing statistics. The paper does not justify why a laboratory-assistant efficiency metric should ignore physical actuation time and the cost of incorrect actions. Without an end-to-end timing analysis, the efficiency results cannot support claims about practical experimental speed.\n“This automation significantly reduces the time and effort compared to manual execution.”\nThis claim concerns an iterative experiment that repeatedly captures images and analyzes results, so scan time and re-scans are central to total wall-clock time. Because the paper’s efficiency metric explicitly removes scan time, it cannot substantiate overall time reduction for the physical workflow. Excluding time for incorrect answers also makes comparisons asymmetric because manual execution necessarily includes troubleshooting and corrective actions. The paper therefore conflates LLM interaction latency with experimental throughput. A valid time-savings claim would require reporting end-to-end time including acquisition, waiting, retries, and recoveries.\n“End-to-end benchmarks provide an all-inclusive evaluation that extends beyond the boundaries of the ML model itself. Rather than focusing solely on a machine learning model’s computational efficiency or accuracy, these benchmarks encompass the entire pipeline of an AI system.” [[1]](#ref1)\nAFMBench is framed as a real-world benchmark that physically executes tasks on AFM hardware, which aligns with end-to-end evaluation principles. The cited guidance emphasizes measuring the entire pipeline, which in AFM includes scanning and hardware wait times. By excluding scan time, the paper’s efficiency metric becomes primarily an interaction-time metric rather than experimental efficiency. By excluding incorrect-answer time, it also fails to capture robustness-related overheads that matter operationally. This mismatch undermines the paper’s interpretation of “efficiency” as experimental efficiency.\n\nReferences:\n[1] <a id=\"ref1\"></a>[ML Systems Book — “Benchmarking AI”](https://mlsysbook.ai/book/contents/core/benchmarking/benchmarking.html)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|GPT|2", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "The paper’s safety/alignment claims (e.g., “sleepwalking” and unauthorized actions) are not causally supported because the implementation executes model-supplied Python via `exec()` without sandboxing and the supplementary logs show AFM-control code executed through the “Image Analyzer” tool, undermining the intended safety boundaries.\n\n“It is worth noting that AI-agent based on GPT-4o, a model known for its reasoning capabilities, exhibit tendencies to perform actions beyond what is instructed, termed as “sleepwalking”.”\nThis statement attributes unsafe actions primarily to the LLM agent, but in instrument-control settings the system’s tool design is a major determinant of safety outcomes. If tools permit arbitrary code execution, unauthorized actions become an architectural inevitability when the model errs. The paper does not separate failures due to model instruction non-adherence from failures enabled by permissive execution pathways. Without that separation, the evidence cannot support the implied causal interpretation that “sleepwalking” is chiefly an LLM property. This weakens the validity of the paper’s safety conclusions and generalization to other SDLs.\n```python\nif dynamic_code:\n    # Safely execute the dynamic code\n    try:\n        exec(dynamic_code)\n        print(\"Dynamic code executed successfully.\")\n```\nThe code executes untrusted dynamic code using `exec()` without restrictions, despite labeling it “Safely execute.” In a lab automation context, this makes the tool capable of arbitrary actions permitted by the Python environment, including direct hardware control. Such a design means safety relies on perfect model adherence, which the paper itself shows is not reliable. The architecture therefore lacks enforceable safety boundaries at the tool interface. This undermines the paper’s framing of observed incidents as mainly an alignment phenomenon rather than a missing sandbox/guardrail problem.\n“This function executes arbitrary code. Calling it with user-supplied input may lead to security vulnerabilities.” [[3]](#ref3)\nThe Python documentation explicitly warns that `exec()` on user-supplied input can create security vulnerabilities, which directly applies when model-generated strings are executed as code. In AILA, the model is effectively the “user” producing executable content, so the warning maps directly to the system’s core control mechanism. The paper does not describe compensating controls such as allowlisted command schemas, command validation, sandboxing, or human approval. Therefore, unsafe actions are plausibly explained by permissive execution design rather than being evidence of an LLM-specific safety failure mode. This substantially weakens the validity of the paper’s causal framing of safety issues.\n\nReferences:\n[3] <a id=\"ref3\"></a>[Python Documentation — Built-in Functions: `exec()`](https://docs.python.org/3/library/functions.html#exec)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|GPT|3", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "The paper’s Methods mis-specify “average friction” and RMS roughness and omit essential calibration details for quantitative friction in physical units, undermining the validity and reproducibility of the mechanical-property measurement component.\n\n“Average friction was calculated using the following formula:\n\\[\nF_{ave} = \\frac{1}{2} \\times (f_{ij} - b_{ij})\n\\]”\nThis equation defines a per-pixel half-difference and does not define an average over the image because it lacks any aggregation across \\(i,j\\). Since the paper reports a scalar “average friction,” the written definition is incomplete or inconsistent with the reported quantity. This is not a minor notation issue because it changes what would be computed by readers implementing the Methods. The manuscript does not specify an aggregation convention elsewhere, so reproductions could diverge. This undermines methodological transparency for a key benchmark output.\n“\\[\nR_{rms} = \\frac{1}{M.N} \\sum_{i=1}^{M} \\sum_{j=1}^{N} (z_{ij} - \\bar{z})^2\n\\]”\nThe RMS roughness equation omits the square root and therefore describes a mean squared deviation rather than a root-mean-square quantity. This changes units and can materially change reported values and interpretations. Because roughness is used as an output in benchmark tasks and case studies, a definitional error affects the validity of conclusions about analysis correctness. Even if the implementation uses the correct formula, the manuscript becomes non-reproducible for readers relying on the written Methods. This is a substantive methodological flaw in the paper’s quantitative analysis description.\n```python\nfriction = 0.5 * (data['Image']['Forward']['Friction force'] - data['Image']['Backward']['Friction force'])\naverage_friction = np.mean(friction)\n...\nrms_roughness = np.sqrt(total_sum / (M * N))\n```\nThe released code computes “average friction” as a mean across pixels, contradicting the manuscript’s friction equation that lacks any averaging operator. The code computes RMS roughness with an explicit square root, contradicting the manuscript’s RMS equation. These inconsistencies mean the paper’s Methods are not a reliable specification of the implemented analysis. For a benchmark paper, alignment between written methodology and executable code is essential for reproducibility. The mismatch raises doubt about whether the manuscript’s reported formulas were validated against the implementation.\n“Therefore, proper calibration of the normal and lateral force constants of the cantilever is crucial in order to extract quantitative, accurate, reliable, and reproducible lateral force values from AFM manipulation experiments.” [[4]](#ref4)\nThis AFM methods statement highlights that quantitative lateral-force reporting depends on calibration, which is directly relevant when reporting friction in nN. The paper’s Methods describe array operations on a friction channel but do not document how lateral sensitivity and torsional constants are handled to ensure physical units are meaningful. Without calibration documentation, friction values may be instrument- and session-dependent and not reproducible across setups. Software verification does not substitute for force calibration unless calibration parameters are specified. This omission undermines the validity of the paper’s “mechanical property measurement” component.\n“The most common surface roughness parameters were evaluated: Ra (average roughness), Rq (root mean square roughness), and Rz (maximum height of the profile).” [[5]](#ref5)\nThis standard definition reinforces that RMS roughness is explicitly a “root mean square” quantity, consistent with requiring a square root in its definition. The manuscript’s RMS formula omits that root, creating a definitional mismatch with common practice. Because roughness values are used as outputs for benchmark tasks, definitional correctness is essential for meaningful evaluation and comparison. Even if the code computes RMS correctly, the written Methods still mislead readers and impede independent replication. This supports the claim that the methodology is not adequately specified.\n\nReferences:\n[4] <a id=\"ref4\"></a>[Çiçek et al., “Quantitative estimation of nanoparticle/substrate adhesion by atomic force microscopy” (Beilstein J. Nanotechnol., 2026; PMCID: PMC12766167)](https://pmc.ncbi.nlm.nih.gov/articles/PMC12766167/)\n[5] <a id=\"ref5\"></a>[Tunca et al., “Comparison of Mechanical, Surface, and Chemical Properties…” (Turk J Orthod., 2025; PMCID: PMC12758443)](https://pmc.ncbi.nlm.nih.gov/articles/PMC12758443/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|GPT|4", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "The AFMBench performance conclusions are not statistically robust because the paper reports point-estimate success rates without confidence intervals or run-to-run variance and uses manual binary scoring without reporting inter-rater reliability or adjudication procedures.\n\n“GPT-4o exhibits exceptional proficiency in documentation-centric operations, achieving a 92% success rate, complemented by robust execution in analysis (71%) and computational tasks (70%).”\nThese success rates are reported as point estimates without any confidence intervals, even though each category has a finite and sometimes small number of tasks. Without uncertainty, readers cannot assess whether differences between categories or models are meaningful or within expected sampling variability. The paper also does not report repeated runs per task, which is important for stochastic LLM agents and tool-driven workflows. As a result, the robustness of conclusions about comparative strengths and weaknesses is unclear. Statistical uncertainty is especially important when using the benchmark to motivate broader design claims.\n“To assess the evaluation of questions in terms of accuracy, we classified the answers provided by AILA into two categories: fully correct answers and incorrect or partially correct answers.”\nA binary rubric can be reasonable, but many AFMBench tasks are multi-step and may admit borderline outcomes that require explicit adjudication rules. The paper notes that “multiple researchers were involved,” but it does not report inter-rater agreement, blinding, or how disagreements were resolved. Without that information, reported accuracy can depend on subjective judgment and may not reproduce across evaluators or labs. This is a major reproducibility issue for a benchmark positioned as a standard evaluation suite. The absence of rater-reliability reporting undermines confidence in the reported success rates.\n“Running each benchmark 5-10 times and reporting statistical measures beyond simple means (including standard deviations or 95% confidence intervals) quantifies result stability…” [[1]](#ref1)\nAgentic systems are probabilistic and can show meaningful run-to-run variability, which makes single-run reporting fragile. The cited guidance reflects common benchmarking practice: report dispersion and confidence intervals to distinguish real effects from noise. The paper reports single percentages and average times, so it is unclear whether findings are stable under resampling or minor environment changes. This matters because the paper draws conclusions about error modes and model differences that could change with repeated trials. Without multi-run and uncertainty reporting, the conclusions are less reliable.\n“The Wilson method for calculating confidence intervals for proportions … is based on inverting the hypothesis test…” [[2]](#ref2)\nAFMBench accuracy is fundamentally a proportion (successes out of tasks) and is naturally accompanied by confidence intervals under standard statistical reporting. The NIST handbook demonstrates that well-established methods exist for proportion confidence intervals, reinforcing that uncertainty reporting is expected. For small subsets (e.g., 10 calculation tasks), confidence intervals can be wide and could materially alter interpretation of performance gaps. The paper’s omission therefore leaves key claims statistically under-supported. This weakens the reliability of comparative conclusions.\n\nReferences:\n[1] <a id=\"ref1\"></a>[ML Systems Book — “Benchmarking AI”](https://mlsysbook.ai/book/contents/core/benchmarking/benchmarking.html)\n[2] <a id=\"ref2\"></a>[NIST/SEMATECH e-Handbook — “7.2.4.1. Confidence intervals”](https://www.itl.nist.gov/div898/handbook/prc/section2/prc241.htm)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|GPT|5", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "The paper overgeneralizes AFMBench-derived results to other disciplines and claims “universal compatibility with API-enabled AFM systems” without evidence, despite the demonstrated system being tied to a specific vendor stack and benchmark task design.\n\n“Our implementation utilizes the DriveAFM instrument (Nanosurf), which is accessed through a Python-based API architecture and designed for universal compatibility with API-enabled AFM systems.”\nThis is a strong portability claim that would require showing the same framework operating across multiple AFM vendors and APIs. The paper does not provide cross-instrument validation, a compatibility matrix, or an explicit vendor-agnostic abstraction layer. In practice, “API-enabled” does not imply a common command model, safety interlocks, or file formats across vendors. Therefore, the evidence in the manuscript does not support “universal compatibility” beyond the demonstrated Nanosurf setup. This overstatement weakens the credibility of the paper’s generality claims.\n“This work’s implications transcend materials characterization. The empirically validated principles—modular architecture (69% multi-tool efficiency), strategic agent deployment (83:17 ratio), and cross-domain integration (80% hybrid task success)—establish design parameters for autonomous laboratories across disciplines.”\nThe reported ratios are descriptive properties of the authors’ curated AFMBench task set and their specific agent/tool decomposition, not established invariants of autonomous lab design. Extrapolating them to other modalities requires evidence that tasks, tools, and constraints are comparable across domains. The paper does not present cross-domain benchmarks, deployments on other instruments, or replications in other labs. Without such evidence, treating these numbers as cross-disciplinary “design parameters” is not justified. This weakens the paper’s broader claims of significance.\n“**Fallacy:** *Benchmark performance directly translates to real-world application performance.*” [[1]](#ref1)\nThe paper uses AFMBench performance statistics to motivate broad conclusions about autonomous laboratories across disciplines. The cited warning highlights that benchmark-to-deployment transfer is often unreliable due to differences in environment, workloads, and constraints. This risk is amplified when transferring from AFM to unrelated lab modalities with different actuation and safety requirements. Without cross-domain validation, benchmark-derived ratios should not be treated as general prescriptions for SDL design. This directly supports the critique that the paper’s generalization exceeds its evidence.\n\nReferences:\n[1] <a id=\"ref1\"></a>[ML Systems Book — “Benchmarking AI”](https://mlsysbook.ai/book/contents/core/benchmarking/benchmarking.html)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "The paper selectively reports results only for GPT-4o and GPT-3.5, omitting data for Claude 3.5 Sonnet and Llama 3.3 70B which are present in the repository and potentially offer significant insights.\n\n\"Systematic evaluation of AILA using two advanced closed source language models—GPT-4o and GPT-3.5-turbo-0125—unveils distinctive execution patterns and operational efficacies.\"\nThe paper explicitly states it evaluates only these two models. However, the accompanying code repository contains full evaluation results for other models.\n```\ncode/Results/Multi-Agent/Claude-3.5-sonnet\ncode/Results/Multi-Agent/Llama-3.3-70B-versatile\n```\nThe existence of these directories in the repository confirms that experiments were conducted with Claude 3.5 Sonnet and Llama 3.3 70B.\n```\nSheet names: ['Sheet1', 'gpt_4o_1', 'gpt-35', 'claude', 'Sheet3', 'Sheet2', 'Llama', ...]\n```\nThe raw results file (`Result_raw_metrices.xlsx`) contains detailed scoring for these omitted models. For instance, the `claude` sheet contains 300 rows of evaluation data. Omitting these results, especially when Claude 3.5 Sonnet is a strong competitor in coding and reasoning tasks, undermines the transparency and comprehensiveness of the benchmark. It prevents the reader from understanding how open-weights models (Llama) or other state-of-the-art closed models (Claude) compare to the GPT series in this domain.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "The benchmark (AFMBench) relies on manual evaluation, which is not scalable, introduces subjectivity, and hinders reproducibility by the broader community.\n\n\"To ensure robustness, we manually evaluated all questions using GPT-4o and GPT-3.5-turbo-0125, verifying the output log files and AFM software results multiple times in collaboration with different researchers to eliminate potential human errors.\"\nManual evaluation is prone to human error and inconsistency, despite the authors' efforts. More importantly, it makes the benchmark difficult to scale or use for automatic regression testing of new models.\n\"A fully correct answer was considered accurate, while any incorrect or incomplete response was deemed incorrect.\"\nThis binary or qualitative classification by humans lacks the precision of automated metrics. In contrast, other scientific benchmarks like SciBench [1] or ChemCrow [2] often employ automated validation (e.g., checking against ground truth values or successful execution of a known reaction path) to ensure objective and reproducible scoring.\n\"Given that some questions require manual inspection of the AFM software to verify whether specific parameters are set correctly...\"\nThis dependency on manual inspection of the GUI/software state indicates a lack of programmatic verification (e.g., via API state checks), which is a standard practice in software and agent benchmarking.\n\nReferences:\n[1] Wang, X., et al. \"SciBench: Evaluating College-Level Scientific Problem-Solving Abilities of Large Language Models.\" arXiv preprint arXiv:2307.10635 (2023). https://arxiv.org/abs/2307.10635\n[2] Bran, A. M., et al. \"ChemCrow: Augmenting large-language models with chemistry tools.\" Nature Machine Intelligence (2024). https://www.nature.com/articles/s42256-024-00832-8", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "The system exhibits a high error rate in code generation, which is a critical bottleneck for an autonomous lab assistant and suggests that the current framework is not yet reliable for autonomous operation.\n\n\"GPT-4o exhibits a total error rate of 20%, with errors distributed across three primary categories: code generation (60%), agent/tool selection (25%), and instruction adherence (15%).\"\nThis statistic implies that 12% of all tasks (60% of the 20% error rate) fail due to code generation issues even with the most advanced model.\n\"GPT-3.5-turbo-0125 demonstrates a markedly higher total error rate of 45%, with errors concentrated in two categories: code generation (66.7%) and agent/tool selection (33.3%).\"\nThe high failure rate in code generation across both models indicates a fundamental weakness in the \"Code Executor\" tool or the prompt engineering strategy. For a system claiming to be an \"Artificially Intelligent Lab Assistant\" capable of \"Autonomous Microscopy Experiments\", such a high failure rate in its primary actuation mechanism (code execution) severely limits its practical autonomy and reliability compared to more robust systems demonstrated in domains like chemistry [3].\n\nReferences:\n[3] Boiko, D. A., et al. \"Autonomous chemical research with large language models.\" Nature 624, 570–578 (2023). https://www.nature.com/articles/s41586-023-06792-0", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "The agent exhibits dangerous \"sleepwalking\" behavior where it performs unrequested actions, posing a significant risk to hardware, which is not adequately addressed by the proposed safety framework.\n\n\"In one of the three recorded errors, GPT-4o exceeded its designated operational limits, performing actions that were not authorized by the provided guidelines. For instance, it carried out potentially risky tip movements while it was only instructed to scan the surface\"\nUnintended physical movements in AFM can destroy the cantilever or damage the sample, which are costly incidents.\n\"In another case, GPT-4o was instructed to capture an image and calculate surface friction. While the image was captured correctly, the system failed to analyse it and switches the AFM to the lateral force mode instead of following clear instructions for a specific task\"\nThis unpredictability, termed \"sleepwalking\" by the authors, highlights a critical safety gap. While the authors mention a \"safety framework\" involving restricted access, the fact that the agent can still execute valid but unrequested commands (like switching modes or moving tips) within the allowed API subset shows that the safeguards are insufficient for autonomous deployment. This aligns with broader concerns about hallucination and alignment in LLMs [4], but the physical consequences here are more severe.\n\nReferences:\n[4] Huang, L., et al. \"A survey on hallucination in large language models: Principles, taxonomy, challenges, and open questions.\" ACM Transactions on Information Systems (2023). https://dl.acm.org/doi/10.1145/3617023", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Gemini|5", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "The paper claims to present \"Autonomous Microscopy Experiments\", but the demonstrated tasks are primarily single-step or limited multi-step workflows initiated by explicit natural language commands, which constitutes automation rather than true autonomy.\n\n\"Upon receiving the query, AILA dissects it into sequential objectives: image acquisition via AFM-HA followed by DHA-led analysis.\"\nThe workflow is reactive to user queries rather than proactive. True autonomy in the context of self-driving labs often implies the ability to generate hypotheses, plan experiments over multiple iterations, and self-correct without human intervention [3].\n\"AFMBench comprises 100 expertly curated experimental tasks... manually designed to rigorously evaluate autonomous AFM operations\"\nThe tasks described (e.g., \"Set image size\", \"Calculate roughness\") are instruction-following tasks. While valuable, framing this as \"autonomous experimentation\" overstates the system's agency. It is more accurately described as a natural language interface for laboratory automation.\n\nReferences:\n[3] Boiko, D. A., et al. \"Autonomous chemical research with large language models.\" Nature 624, 570–578 (2023). https://www.nature.com/articles/s41586-023-06792-0", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "Many AFM operation software or packages already integrate data analysis functionalities. What is the rationale for including a separate data handler tool in AILA? Both AFM experiments and data analysis can be done directly using the same vendor software or package, particularly for the examples provided in this manuscript.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "What additional or advanced data analysis capabilities does the data handler offer beyond those already existing in AFM vendor software or package?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "The inclusion of a safety framework is a great development. However, if it is constrained to predefined documentation, it may limit the flexibility for designing experiments not covered in the documentation, particularly for new experiment designs.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "What is the generic algorithm used for optimizing imaging parameters? Also, if a different prompt or a sample with distinct morphology is used in the experiment, does AILA select a different optimization algorithm?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "Similar questions, how consistent is the edge detection algorithm applied by AILA? Does the selection of the algorithm depend on real-time results, or is the same method consistently applied across different samples?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "The consistency and adaptability of algorithm selection might directly impact the reliability of AILA. A more detailed discussion on how AILA ensures robustness in algorithm selection and data analysis should be added.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "Prior research has explored the use of LLMs, such as ChatGPT, for AFM operations. The authors should acknowledge and discuss these efforts, such as https://iopscience.iop.org/article/10.1088/2632-2153/ad52e9/meta. Previous work has also identified similar challenges, such as LLMs performing well in single-step experiments but struggling with multi-step processes.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Human_1|9", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "In addition, given that this manuscript focuses on LLM-driven autonomous AFM, prior efforts in autonomous AFM development should be properly referenced.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "This manuscript presents a dynamic routing framework that allows the agent to choose the next agent to use. However, the author didn’t discuss how such a dynamic multiagent system actually work and how it performs comparing to single-agent scenario.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "It is relatively strange to discuss the performance of different LLMs before introducing how it actually solves AFM problems.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "AFM is an analytical method, and it is used for material analysis to reveal structure-property relationships. However, the authors focused on developing LLM system to improve the autonomy of the AFM analysis, but didn’t give real-world examples show how it actually perform AFM analysis, and gives the analysis conclusions like human experts, which is the ultimate goal of such analysis method. It is suggested that authors should add 1-2 real-world examples.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "In Figure 3 and lines 226-233, the authors discuss the temporal efficiency of various LLMs. Is the task completion time mentioned here the sum of the LLM’s response time and the tool execution time? If so, considering that the authors interact with the LLM through network APIs, the network environment of the AILA system and the resources available on the LLM servers could impact the LLM’s response time. Therefore, this comparison of results may not accurately reflect the LLM’s performance and may need more rigorous handling.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "The authors mention that Claude-3.5-sonnet exhibits subpar agentic capabilities, primarily due to agent and tool selection errors. This issue may arise from the integration challenges between Anthropic’s Claude series models and frameworks like LangChain and LangGraph, especially concerning functionalities like function calls. These integrations might not fully leverage Claude-3.5-sonnet’s inherent strengths. I hope the authors can further analyze the reasons for Claude 3.5-sonnet’s poor performance from this perspective. Additionally, Anthropic’s recent introduction of the Model Context Protocol (MCP) offers a standardized method for connecting AI models with external data sources and tools, potentially enhancing agentic performance. Integrating MCP with Claude has demonstrated improved multi-agent applications, such as Manus. I also hope the authors can conduct research and discussion on this.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "The authors mention safety alignment in SDLs and implement strict operational boundaries to mitigate safety risks. I suggest that after identifying risky actions, an additional human review mechanism could be introduced. For instance, if an expert detects an issue, they could suggest corrections (input via natural language), enabling a “human-in-the-loop” interaction that ensures continuous, safe operation of the workflow, rather than directly terminating the task when candidate actions beyond operational boundaries.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "The level of detail and readability of the Supplementary Materials need improvement. (1) A table of contents is missing. (2) The output logs from the AILA system are too lengthy and appear to be directly copied from terminal outputs. These should be organized and refined to enhance readability. (3) The detailed process and results of expert evaluation of AILA’s performance on AFMBench, including how researchers determined whether the answers provided by AILA were entirely correct, incorrect, or partially correct, should be included in the supplementary materials and referenced in the main text. If too many details, representative examples can be included.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "However, experimentally, the scope of the current framework is limited to scans in one location and very standardized analysis. From an applied AI perspective, the agent and tool sets are also highly task-specific and their performance depends greatly on the specificity of the prompts. With the addition of artifact/anomaly detection tools such as those developed by the autonomous microscopy works cited, as well as an additional agent that iteratively debugs generated code to control the instrument, the agentic framework has the potential to be applicable to real-world experiments.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "In the evaluation of agent performance, is each task given to each model once? Or if the exact same tasks are repeated, how consistent is the agent response each time?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "The current focus seems to be on the agents completing the task in one go. If an agent cannot complete the task, it knows, with appropriate prompting, to output NEED HELP to invoke the other agent. Is there a way for the user to provide additional context in such situations, and for the user’s feedback to be stored to improve the agent?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "In Table S2, we see detailed vs. concise prompts for the same task. The concise prompt fails but the detailed prompt is a step-by-step guide for the agents. What is the advantage in using an agentic framework here when presumably an LLM with access to tools can follow instructions and execute?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "Relatedly, the structure of the framework seems to be two agents, which each have access to two tools. How does the performance compare to if one agent was given all tools? Or if there was an agent for each tool?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "More generally, the distinction between tool and agent is not clear. The authors themselves seem to use the two interchangeably, see for e.g. line 701. Figure 2 and the discussion around it centers on this distinction.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Human_3|7", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "Regarding model-specific limitations, could iterative debugging improve results for cases where the failure mode is code generation? I suggest some quantification of the distribution of types of bugs and a clarification of how that may be addressed beyond needing an entirely different LLM.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Human_3|8", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "There is a lot of emphasis placed on the model evaluation. At the rate of current progress, models become obsolete in a few months. E.g. Claude 3.5 and GPT-3.5 have been succeeded by newer models.\\n\\na. It would be nice to see a focus on evaluation metrics rather than specific models", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Human_3|9", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "One of the critical results presented is the demonstration of experimental workflows beyond single scan acquisition. In figure 5, the prompt given is “Optimize the values of the P, I, and D gains using a genetic algorithm. Do not correct the baseline.” This is quite specific. Is there any analysis on whether the agentic framework could complete the task without being told to optimize the PID, but rather more generically with instructions to optimize for image clarity and/or stability between scans? Or without specifying the algorithm to be used?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Human_3|10", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "The first three discussion paragraphs summarize and repeat many points that were scattered throughout the results section. I suggest a more in-depth discussion of the last two points instead, as they seem more relevant to addressing strengths (modularity) and limitations (limited functionality) of the framework.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Human_3|11", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "AFM parameter optimization:\\n\\na. Not clear if the genetic algorithm code was provided or written by the LLM. If the former, why not evaluate the models on their ability to write code to solve problems?\\n\\nb. What happens if you add a code writer in addition to a code executor?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Human_3|12", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "Does the current workflow call predefined code blocks from the documentation?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|39|Human_3|13", "source": "prb", "split": "test", "paper_id": "prb39", "comment": "How can others evaluate their models or agents on this benchmark? By definition, the benchmark should be accessible to anyone.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|Claude|1", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "The paper employs a User Input Principle (UIP) data augmentation method that generates 1000-fold synthetic data points from 162 real samples by adding Gaussian noise to both input features and output labels. This augmentation strategy may compromise the validity of model evaluation, as synthetic training samples in the augmented dataset could be artificially close to test samples, leading to overly optimistic performance estimates that do not reflect true generalization capability.\n\n\"In this study, the UIP method was adopted to synthesize 1,000-fold virtual data points by introducing Gaussian noises in the vicinity of 162 real data points collected during the active learning loops.\"\nThe paper generates 162,000 synthetic data points from only 162 real experimental samples. When training data is expanded by 1000x via Gaussian noise addition, the augmented points can densely populate the parameter space around real training samples. If test samples happen to fall within these noise-perturbed regions, the model's apparent accuracy on test data may be inflated because the model has effectively seen very similar synthetic points during training, rather than truly learning generalizable relationships.\n\"To overcome the overfitting challenges upon the use of a small dataset, we employed a data augmentation method, specifically the UIP method, to synthesize virtual data points in the vicinity of real data points collected during the active learning loops.\"\nWhile the authors claim data augmentation addresses overfitting, the specific implementation (x_std=0.05, y_std=0.05 as shown in code) creates synthetic points that span approximately ±5% variations around original samples. Standard practice in machine learning recommends that augmentation be performed only on training data and that evaluation metrics be computed strictly on real, unaugmented test data. The paper does not clearly demonstrate that test samples are sufficiently distant from the augmented training distribution to ensure unbiased performance estimation.\n\n* Quote from code (utils/da.py):\n```python\ndef augmente_data(raw_df, x_cols, y_cols, n_augmented=0,\n                  y_std_cols=None, x_std=0, y_std=0,\n                  id_col='sID', da_col='DA#', random_state=None):\n    ...\n    noisy_x = pd.DataFrame(rng.normal(raw_df[x_cols], x_std_df), columns=x_cols)\n    noisy_y = pd.DataFrame(rng.normal(raw_df[y_cols], y_std_df), columns=y_cols)\n```\nThe code reveals that both input features (composition labels) and output labels (σ30, R0) are perturbed with Gaussian noise. Adding noise to outputs during augmentation is particularly problematic, as it introduces artificial label variation that may not correspond to actual measurement uncertainty. Standard data augmentation practices typically only transform inputs while preserving original labels. This approach may cause the model to learn artificial noise patterns rather than true physical relationships.\n\"Towards the end of active learning loops, both MAE and MRE values were stabilized and gradually approached toward the measurement variations of σ30 (~1.1 kPa) and R0 (~10.1%).\"\nThe authors present model error approaching measurement noise as evidence of high model quality. However, achieving error close to measurement noise with only 162 real samples and 1000x synthetic augmentation is unusual and may instead indicate that the evaluation methodology does not adequately measure true generalization. In standard ML practice, when augmentation is used, careful protocols must ensure the test set remains independent from all augmented data [[1]](#citation-list).\n\nReferences:\n[1] KDNuggets. \"Avoiding Overfitting, Class Imbalance, & Feature Scaling Issues: The Machine Learning Practitioner's Notebook\" - https://www.kdnuggets.com/avoiding-overfitting-class-imbalance-feature-scaling-issues-the-machine-learning-practitioners-notebook", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|Claude|2", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "The paper evaluates the ANN prediction model using a test set that appears to contain only approximately 15-20 data points (Table S4), which is statistically insufficient to reliably assess model generalization. Furthermore, no external validation on independently collected samples is performed, making it unclear whether the reported MAE of 1.5 kPa and MRE of 18.4% represent genuine predictive capability or are artifacts of overfitting to a limited parameter space.\n\n\"the accuracy of multi-property predictions was assessed using a set of testing data points, which were never input into the model (see Table S4). For each testing data point, the ANN model provided the predicted σ30 and R0 values based on the 'composition' and 'loading' labels.\"\nWhile the authors state that test data points were held out from training, the small number of test samples visible in Table S4 (approximately 15-20 entries based on the supplementary materials) provides very limited statistical power to assess model performance. With such a small test set, performance metrics like MAE and MRE have high variance and may not reliably represent the model's expected performance on new samples. Standard practices in materials informatics recommend larger test sets or rigorous cross-validation schemes to provide robust performance estimates [[2]](#citation-list).\n\"the MAE (that assessed the accuracy of σ30 prediction) continually decreased from 2.5 to 1.5 kPa (Fig. 2e, top), and the MRE (that assessed the accuracy of R0 prediction) decreased from 49.0% to 18.4% (Fig. 2e, bottom).\"\nThe reported performance improvement during active learning is evaluated on the same test set throughout all 8 loops. As the model sees progressively more data from the same experimental setup and parameter space, performance improvement on a fixed test set may reflect the model's coverage of that specific space rather than generalizable predictive power. External validation using independently fabricated samples from different batches or conditions would be necessary to confirm the model's robustness [[3]](#citation-list).\n\"the champion model demonstrated exceptional prediction capabilities and allowed for two-way design tasks, including accurately predicting the σ30 and R0 values of a conductive aerogel and suggesting suitable fabrication parameters to produce conductive aerogels that met specific property requirements.\"\nThe strong claims about \"exceptional prediction capabilities\" require more rigorous validation. In materials machine learning, where data is expensive to collect and experimental variability is high, best practices call for external validation using data collected under different conditions or from different laboratories to ensure model robustness. The absence of such validation in this work limits confidence in the generalizability of the reported model performance [[4]](#citation-list).\n\n* Quote from Note S5 in supplementary: \"The SVM classifier was trained using 264 grades, which achieved a prediction accuracy of 95% based on 40 testing data points.\"\nFor the SVM classifier, 40 test points were used for evaluation. While this is larger than the apparent ANN test set, the overall validation strategy relies on a single train-test split rather than cross-validation or repeated experiments. Single-split evaluations are known to produce unstable performance estimates, especially with small datasets. The absence of confidence intervals or variance estimates for the reported metrics makes it difficult to assess the reliability of the performance claims [[5]](#citation-list).\n\nReferences:\n[2] Zhang, Y. & Ling, C. \"A strategy to apply machine learning to small datasets in materials science.\" npj Computational Materials 4, 25 (2018) - https://www.nature.com/articles/s41524-018-0081-z\n[3] Lookman, T. et al. \"Active learning in materials science with emphasis on adaptive sampling using uncertainties for targeted design.\" npj Computational Materials 5, 21 (2019) - https://www.nature.com/articles/s41524-019-0153-8\n[4] Li, K. et al. \"Probing out-of-distribution generalization in machine learning for materials.\" Communications Materials 6, 9 (2025) - https://arxiv.org/html/2601.08486v1\n[5] Harrington, P. \"Evaluation of machine learning: Train-test splits and cross-validation.\" (2018) - Referenced in Nature Scientific Reports regarding machine learning evaluation protocols", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|Claude|3", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "The paper presents finite element (FE) simulations as validation of the SHAP-derived insight that mixture loading strongly influences compressive strength. However, the FE model construction involves tuning parameters (β_imp) and uses geometric parameters extracted from the same experimental samples being validated, creating a methodological circularity where the simulation is effectively fitted to match experimental results rather than providing independent verification.\n\n\"A constant number of wall discontinuities was seeded for all three FEA models, with the exact number chosen as a tuning parameter.\"\nThe use of a tuning parameter (β_imp = 0.3) that controls the number of discontinuities in the FE model means the simulation has a free parameter that can be adjusted to match experimental results. When a computational model has tunable parameters selected to achieve agreement with experimental data, it cannot serve as independent validation of physical relationships. Instead, it becomes a fitting exercise where good agreement is engineered rather than discovered.\n\n* Quote from Note S9 in supplementary: \"the cellular structure of a conductive aerogel was represented using a two-dimensional staggered brick-wall architecture, whose dimensions were extracted from the SEM images in Fig. 4c.\"\nThe FE model geometry is directly derived from SEM images of the experimental samples whose mechanical properties are being validated. The pore dimensions, wall thickness, and aspect ratios used in the simulation come from measuring the same samples being predicted. This creates a situation where experimental data is used to construct the model, and then the model is said to validate those same experimental observations, which constitutes circular reasoning.\n\n* Quote from Table S8: \"The wall of conductive aerogels was modeled as an isotropic material, whose mechanical properties were acquired experimentally\"\nThe FE model uses experimentally measured Young's modulus (3,440.7 MPa), Poisson's ratio (0.5), and other parameters from the actual samples. When both the geometry and material properties come from the experimental samples being validated, the simulation essentially reproduces known results rather than providing independent predictive validation. A more rigorous approach would use literature values or independent measurements.\n\"By exerting a vertical compressive strain of 30% on three FE models, the σ30 values were simulated in Fig. 4b, showing good agreement with the experimentally characterized σ30 values.\"\nThe \"good agreement\" between FE predictions and experimental results is presented as validation of the SHAP interpretation. However, given that the FE model uses tuning parameters and experimental inputs, this agreement is expected by construction. The claim that FE simulations validate the ML-derived correlation between mixture loading and compressive strength is weakened because the FE model was effectively parameterized using experimental knowledge about these samples.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|Claude|4", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "The paper compares the ANN committee model only against basic machine learning algorithms (linear regression, decision tree, gradient-boosted decision tree, random forest) without benchmarking against state-of-the-art methods designed for small-dataset materials science problems, such as Gaussian Process regression, Bayesian optimization, or transfer learning approaches. This limited comparison makes it difficult to assess whether the proposed methodology represents a genuine advancement over existing approaches.\n\n\"Among other models based on linear regression, decision tree, gradient-boosted decision tree, random forest algorithms, the ANN model demonstrated the lowest MAE and MRE values (Fig. 2e).\"\nThe comparison algorithms are relatively basic machine learning methods. For small-dataset problems in materials science, Gaussian Process (GP) regression has been widely adopted due to its ability to provide uncertainty quantification and perform well with limited data. GP-based Bayesian optimization is particularly popular in materials discovery applications. The absence of comparison with such established methods makes it unclear whether the proposed ANN committee approach offers genuine advantages over standard alternatives [[6]](#citation-list).\n\n* Quote from Note S3 in supplementary: \"ANN committee: As indicated in Fig. 2e, the prediction models based on alternative algorithms struggled to accurately predict the σ30 and R0 values of conductive aerogels... our prediction model, which incorporated an ANN committee, demonstrated the lowest MAE of 1.5 kPa\"\nWhile the ANN committee outperforms the basic algorithms tested, the comparison does not include methods specifically designed for small-dataset scenarios. Recent literature on machine learning in materials science has demonstrated that ensemble methods, transfer learning, and GP-based approaches can achieve competitive or superior performance on similar small-dataset problems [[7]](#citation-list). Without such comparisons, the significance of the improvement cannot be properly contextualized.\n\n* Quote from Table S7 in supplementary: \"Comparison of our AI/ML integrated approach for conductive aerogels with the state-of-the-art works.\"\nTable S7 compares the work with traditional \"design of experiment\" approaches rather than with competing machine learning methodologies. While this comparison demonstrates advantages over manual optimization, it does not establish whether the specific ML architecture and active learning strategy outperform alternative computational approaches. A comprehensive comparison would include recent active learning methods and uncertainty-aware models that have shown promise in similar materials design tasks [[8]](#citation-list).\n\nReferences:\n[6] Schmidt, J., Marques, M.R.G., Botti, S. & Marques, M.A.L. \"Recent advances and applications of machine learning in solid-state materials science.\" npj Computational Materials 5, 83 (2019) - https://www.nature.com/articles/s41524-019-0221-0\n[7] Active Learning Strategies for Efficient Machine Learning in Materials Science (2025) - https://www.arxiv.org/pdf/2601.06916\n[8] \"Artificial Intelligence Empowered New Materials: Discovery, Design, and Synthesis\" - Springer Nature (2025) - https://link.springer.com/article/10.1007/s40820-025-01945-4", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|GPT|1", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "The manuscript’s core ANN “champion model” accuracy claims are not sufficiently valid because the described UIP-based data augmentation perturbs not only inputs but also measured property labels and then evaluates with cross-validation without specifying leakage-avoiding splits, which can yield overly optimistic performance estimates for the active-learning pipeline.\n\n“To synthesize virtual data points, Gaussian noises were introduced in the proximity of the composition, mechanical, and electrical labels based on our experimental observations. Afterward, both real and virtual data points were utilized as training data points for an ANN-based model using 4-fold cross-validation.”\nThis explicitly states that the augmentation procedure perturbs the labels (mechanical and electrical outputs) rather than generating new measurements, which is fundamentally different from adding more independent training data. Injecting noise into the targets creates pseudo-observations whose values are not experimentally verified, so improved fit can reflect learning the augmentation scheme rather than learning true structure. The manuscript does not describe any safeguards (e.g., grouped splits) to ensure that augmented variants of a real point cannot appear in both training and validation folds, which is a well-known pathway to inflated cross-validation scores. Because the virtual points are generated “in the vicinity” of each measured point, their feature/label neighborhoods will be highly overlapping, making leakage especially consequential. As a result, the reported MAE/MRE improvements with higher virtual-to-real ratios cannot be taken as robust evidence of real-world generalization without a leakage-proof evaluation protocol.\n“In this study, the UIP method was adopted to synthesize 1,000-fold virtual data points by introducing Gaussian noises in the vicinity of 162 real data points collected during the active learning loops.”\nThis confirms that the effective dataset size is expanded by three orders of magnitude from only 162 experimentally realized compositions, primarily by sampling noise around them. Such a procedure does not add new independent constraints on the underlying fabrication–property map; it mostly densifies local neighborhoods with correlated pseudo-points. Consequently, the claimed “approximately 160,000 data points” do not correspond to 160,000 experiments and should not be interpreted as comparable evidence to a genuinely large dataset. In small-data materials ML, synthetic augmentation can be helpful when it respects invariances and does not fabricate new labels, but here the label perturbation directly alters the supervised signal. Without demonstrating that conclusions hold when training only on real points (or when validating on truly novel compositions), the validity of the learned mapping remains uncertain.\n```python\ndef augmente_data(raw_df, x_cols, y_cols, n_augmented=0,\n                  y_std_cols=None, x_std=0, y_std=0,\n                  id_col='sID', da_col='DA#', random_state=None):\n    if y_std_cols is not None:\n        y_std_df = raw_df[std_cols]\n    else:\n        y_std_df = np.ones(raw_df[y_cols].values.shape) * y_std\n\n    x_std_df = np.ones(raw_df[x_cols].values.shape) * x_std\n\n    raw_df = raw_df.copy()\n    raw_df[da_col] = 0\n\n    noisy_dfs = [raw_df, ]\n    rng = np.random.default_rng(random_state)\n\n    for i in range(n_augmented):\n        noisy_x = pd.DataFrame(rng.normal(raw_df[x_cols], x_std_df), columns=x_cols)\n        noisy_y = pd.DataFrame(rng.normal(raw_df[y_cols], y_std_df), columns=y_cols)\n        noisy_xy = noisy_x.join(noisy_y)\n        noisy_sid = raw_df[[id_col]].copy()\n        noisy_sid[da_col] = i + 1\n        noisy_df = noisy_sid.join(noisy_xy).reset_index(drop=True)\n        noisy_dfs.append(noisy_df)\n    final_df = pd.concat(noisy_dfs, ignore_index=True).sort_values(by=[id_col, da_col]).reset_index(drop=True)\n    return final_df[[id_col, da_col] + x_cols + y_cols]\n```\nThis released code shows that the augmentation samples both inputs and outputs from Gaussians centered on the measured values (i.e., it directly fabricates new target labels). In standard supervised learning, one can inject noise into inputs as a robustness regularizer, but fabricating new outputs typically requires a forward model or a physical constraint; otherwise, it can blur or distort the true mapping. The function also preserves an `id_col` (`sID`) while generating many augmented variants, implying that proper evaluation would need group-aware splitting so that all variants of an original sample stay in the same fold. The manuscript does not provide the corresponding training/evaluation code demonstrating that such grouped splitting was done for the reported cross-validation results. Therefore, it is plausible that cross-validation performance is systematically optimistic due to near-duplicate leakage, which directly threatens the validity of the paper’s central modeling claims.\n“We can generate new (x, y) pairs easily just by transforming the x inputs in our training set.” [[2]](#ref-2)\nThis describes a common and principled form of dataset augmentation: apply transformations to inputs while preserving the underlying label, thereby encoding invariances of the task. In the reviewed manuscript, the augmentation explicitly perturbs the labels (e.g., σ30 and R0) rather than holding them fixed under input perturbations, which is not aligned with the standard augmentation rationale. Perturbing labels can be appropriate when modeling annotation noise or performing label smoothing, but then evaluation must explicitly account for the induced uncertainty and should not be conflated with acquiring additional data. The manuscript frames the procedure as a way to “counteract potential overfitting” and to create a vastly larger “database,” which risks overstating the evidentiary weight of synthetic points. This contrast with common practice supports the criticism that the augmentation strategy, as described, does not by itself justify strong claims of predictive accuracy.\n“Data leakage occurs when information that would not be available at prediction time is used when building the model. This results in overly optimistic performance estimates, for example from cross-validation…” [[1]](#ref-1)\nThe manuscript’s augmentation creates many points that are deterministically derived from the original measured datapoints (same local neighborhood in both inputs and outputs), so leakage across folds becomes a direct risk if folds are not constructed at the level of original experiments. In such settings, cross-validation can become a test of interpolation among near-duplicates rather than a test of generalization to new compositions. The manuscript does not specify group-aware splitting or an equivalent safeguard, and it reports performance improvements as the virtual-to-real ratio increases, which is consistent with a regime where leakage or near-duplicate overlap can dominate. Because the key claims rely on small absolute errors and “high prediction accuracy,” overly optimistic estimates would materially change the conclusions. Therefore, the paper needs an explicit, leakage-resistant evaluation protocol (and ideally a fully held-out set of truly novel recipes) to support its central validity claims.\n“The key idea behind active learning is that a machine learning algorithm can achieve greater accuracy with fewer training labels if it is allowed to choose the data from which it learns.” [[3]](#ref-3)\nThis quote emphasizes that active learning’s core promise is improved performance with fewer *real* labels by selecting informative datapoints for labeling. In the reviewed manuscript, most of the nominal dataset growth is achieved by generating many virtual points via Gaussian perturbations of both inputs and measured outputs, which is a different mechanism than acquiring new labeled experiments. As a result, improvements attributed to “active learning loops with data augmentation” are difficult to interpret, because they conflate the benefit of additional real experiments with the effect of synthetic label jitter. This distinction matters for validity: inverse design depends on learning the true fabrication–property relationship, not primarily a smoothed proxy created by injected output noise. Without reporting performance on truly novel, non-augmented held-out recipes (or demonstrating fold-grouping that prevents near-duplicate leakage), the paper’s central active-learning-driven accuracy claims remain under-supported.\n\nReferences:\n[1] <a id=\"ref-1\"></a> [scikit-learn documentation: “Common pitfalls and recommended practices” (Data leakage section)](https://scikit-learn.org/stable/common_pitfalls.html)\n[2] <a id=\"ref-2\"></a> [Goodfellow, Bengio, Courville. *Deep Learning* (Chapter 7: Regularization for Deep Learning; Dataset Augmentation section)](https://www.deeplearningbook.org/contents/regularization.html)\n[3] <a id=\"ref-3\"></a> [Settles, B. “Active Learning Literature Survey” (2009)](http://burrsettles.com/pub/settles.activelearning.pdf)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|GPT|2", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "The paper’s conclusions about “high electrical conductivity” and strain-stable Joule heating are not fully supported because the electrical label used for learning and design is a two-electrode resistance measurement (R0) that is sensitive to contact and geometry, yet it is treated as a direct proxy for conductivity in the model and design criteria.\n\n“Next, by using a two-electrode system (with a 1-cm gap between electrodes), the initial electrical resistance of each conductive aerogel (abbreviated as R0) was measured, and the average R0 value from 3–4 aerogel replicates was recorded as the “electrical” label.”\nThis sentence shows the model’s electrical target is a two-terminal resistance measured across a fixed electrode gap, not a geometry-normalized conductivity or resistivity. Two-electrode measurements conflate sample resistance with electrode contact resistance and wiring contributions, especially for porous, compressible materials where contact area can vary with placement and compression. Because the ANN is trained to predict R0 and the inverse-design targets are formulated in terms of R0 thresholds, any systematic contact/geometry variability directly propagates into both the learned mapping and the “designed” recipes. The manuscript does not describe a four-probe (Kelvin) method, nor does it specify how sample dimensions, electrode pressure, or contact reproducibility are controlled for R0 across the large experiment set. This makes it difficult to interpret R0 as an intrinsic material property and undermines claims that the model designs “high conductivity” aerogels in a way comparable across studies.\n“First, two property requirements were considered: (I) compatible compressive strength … and (2) high electrical conductivity for efficient Joule heating (R0 < 20 Ω).”\nHere the paper equates “high electrical conductivity” with a threshold on the two-electrode resistance R0, which is not generally equivalent without controlling geometry and contact conditions. In particular, resistance thresholds depend on the sample’s cross-sectional area and thickness as well as electrode configuration, so a low R0 does not uniquely imply high intrinsic conductivity. This matters because the paper frames the ML system as enabling “programmable electrical properties,” which suggests transferability beyond a single test geometry. The statement also directly ties design decisions (which recipes are considered successful) to R0, so any measurement artifact or contact dependence becomes a selection bias in the showcased “strain-insensitive” aerogel. Without demonstrating that the designed aerogels maintain low resistivity under standardized, contact-insensitive measurements, the strength of the conductivity-based conclusions is reduced.\n“One of the primary advantages of using a four-point probe to perform electrical characterization is the elimination of contact and wire resistances from the measurement.” [[4]](#ref-4)\nThis establishes a widely used measurement principle: four-terminal sensing is specifically designed to remove contact and lead resistances that contaminate two-terminal measurements. Since the manuscript relies on a two-electrode setup for R0, it does not benefit from this elimination and therefore risks conflating intrinsic aerogel conduction with contact effects. This is particularly important in the paper’s context because the target application involves repeated compression and “pressure insensitivity,” where contact conditions can change. If contact resistance changes under compression, the measured “strain-insensitive” electrical response could partially reflect electrode-interface behavior rather than bulk network stability. The lack of a contact-insensitive conductivity measurement protocol therefore weakens the validity of the electrical-property claims and their generality.\n\nReferences:\n[4] <a id=\"ref-4\"></a> [Ossila: “Calculate Sheet Resistance Using the Four‑Probe Method” (Eliminating Contact Resistance section)](https://www.ossila.com/pages/sheet-resistance-theory)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|GPT|3", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "The reported improvement and interpretation of electrical prediction accuracy are not statistically sound because the manuscript defines “mean relative error (MRE)” using a nonstandard ratio of logarithms that can diverge (e.g., near log(R0)=0) and is then compared to measurement “percentage” variation, making the electrical model-performance claims unreliable.\n\n“MRE = \\frac{1}{N} \\sum_{i=1}^{N} \\left| \\frac{\\log(predicted\\ R_0^i) - \\log(R_0^i)}{\\log(R_0^i)} \\right|”\nThis formula divides the log-scale error by \\(\\log(R_0^i)\\), which is an unusual normalization and is not the typical way to measure relative error on a log-scaled quantity. The denominator can become arbitrarily small when \\(R_0^i\\) is near 1 Ω (since \\(\\log(1)=0\\)), which would make the metric unstable or undefined for values in that neighborhood. Even when defined, this metric weights errors in a way that depends on the absolute value of \\(\\log(R_0)\\) rather than on the physical scale of \\(R_0\\) itself, complicating interpretation across a range spanning many orders of magnitude. Because the paper later reports MRE as a “%” quantity, this nonstandard definition risks conflating logarithmic scaling with percentage error. Overall, the metric choice and its interpretation directly affect the paper’s conclusions about electrical prediction accuracy and approaching measurement noise.\n“Throughout 8 active learning loops, … the MRE (that assessed the accuracy of R0 prediction) decreased from 49.0% to 18.4% … and gradually approached toward the measurement variations of … R0 (~10.1%).”\nThis passage interprets the MRE as a percentage and compares it directly to a stated measurement variation of ~10.1%, implying they are commensurate quantities. However, the MRE definition is not a conventional percentage relative error (it is a ratio of logarithms), so its numeric values are not directly comparable to a percent coefficient of variation measured on R0. The comparison could therefore mislead readers into believing the model has nearly reached the experimental noise floor when, under a standard metric (e.g., absolute log error or relative error), the conclusion might differ. Because this statement is used to argue “high prediction accuracy” and model maturation, it materially affects the reliability of the manuscript’s main claims. A statistically appropriate practice would be to report standard metrics for multiplicative-scale targets (e.g., MAE on log(R0) or RMSLE) and to report uncertainty intervals that align with the measurement process.\n“MSLE(y, ŷ) = \\frac{1}{n\\_\\text{samples}} \\sum_{i=0}^{n\\_\\text{samples} - 1} (\\log_e (1 + y_i) - \\log_e (1 + \\hat{y}_i) )^2.” [[5]](#ref-5)\nThis provides an example of a standard, well-defined log-scale error metric that compares log-transformed values via differences, without introducing a potentially singular normalization by \\(\\log(y)\\). For targets spanning orders of magnitude (as R0 does in the manuscript), using a log-error metric is common, but it should remain numerically stable across the whole range. In contrast, the manuscript’s MRE divides by \\(\\log(R_0)\\) and therefore changes the effective weighting across the target range in a way that is not clearly motivated. Using a standard metric like MSLE/RMSLE (or MAE on \\(\\log R_0\\)) would make performance comparable and interpretable, and it would allow a principled comparison to measurement variability on the same scale. The existence of standard alternatives strengthens the criticism that the manuscript’s chosen MRE and its “%” interpretation are statistically problematic.\n\nReferences:\n[5] <a id=\"ref-5\"></a> [scikit-learn documentation: “Metrics and scoring: quantifying the quality of predictions” (MSLE/MAPE definitions)](https://scikit-learn.org/stable/modules/model_evaluation.html)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|GPT|4", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "The paper’s computational results are not reproducible from the provided code bundle because the notebooks depend on unspecified external datasets and trained-model artifacts, and the provided “SVM classifier” training code described in the supplement is inconsistent with what the linked notebook actually implements.\n\n“We have recorded the Python code used for training the SVM model available on GitHub for open-source use. It can be accessed at https://github.com/oshin71/Programmable-MXene-Aerogel/blob/main/design_boundary.ipynb.”\nThis statement asserts that the SVM classifier training code needed to reproduce the feasibility model is available in a specific notebook. Reproducibility requires that the linked code actually implement the described method (an SVM classifier on A/B/C grades) and that the necessary input data be included or clearly documented. However, the notebook content (see code evidence below) reads a dataset from a local path and then fits an SVR regressor, which is not a classifier and does not match the described three-grade classification problem. This mismatch makes it unclear what exact model produced the reported “95%” accuracy and the feasibility heatmaps. Because the SVM feasibility filter is an upstream gatekeeper for the entire active-learning and inverse-design workflow, lack of reproducibility here threatens the validity of downstream claims.\n```python\nfeas_df = pd.read_csv('data/db_train.csv')\n\nfrom skopt import BayesSearchCV\nfrom sklearn.model_selection import RepeatedKFold, RepeatedStratifiedKFold\n\nsearch_space = {\n    'C':     (1e-1, 1e+2, 'log-uniform'),\n    'gamma': (1e-5, 1e+1, 'log-uniform')\n}\n\nfeas_models = {}\nfor col in c_tags:\n    sub_df = feas_df[(feas_df[col] == 1)]\n    opt = BayesSearchCV(sklearn.svm.SVR(), search_space, n_iter=16, random_state=0,\n                        cv=RepeatedKFold(n_splits=5, random_state=0))\n\n    opt.fit(sub_df[['CNF', 'MXN']], sub_df['score_ternary'])\n    feas_models[col] = opt\n```\nThis notebook cell depends on a local CSV file (`data/db_train.csv`) that is not described in the repository instructions, preventing an independent reader from running the analysis as-is. More importantly, it uses `sklearn.svm.SVR()` (support vector regression) and fits a continuous target `score_ternary`, which does not implement the manuscript’s described “SVM classifier” trained on discrete A/B/C grades to output an A-grade probability. While the authors may have additional, unshared code for the classifier, the materials provided in this review package do not support reproduction of the stated classifier or its evaluation. Because the supplement points to this notebook as the source of the SVM training code, the inconsistency is not merely a documentation gap; it is a direct reproducibility failure. This materially impacts confidence in the paper’s claimed feasibility filtering and the derived “feasible parameter space.”\n```python\nf_model = f'data/eps30_models/{model_name}.model'\nmodel = tf.keras.models.load_model(f_model)\n```\nThis shows that the active-learning notebook expects pre-trained neural network model files under `data/eps30_models/`, rather than providing code to train them from the reported experimental data. Without these model artifacts (or a training script that reconstructs them deterministically), an independent reader cannot reproduce the committee predictions or uncertainty estimates used to drive acquisition. This is especially problematic because the paper’s central contribution is an ML-driven closed-loop workflow; if the trained models are required but not distributed, the workflow cannot be independently validated. The manuscript also reports performance improvements across active-learning loops, which would require access to per-loop training states and data splits. The absence of these artifacts therefore blocks verification of key empirical claims.\n```python\ntrain_df = pd.read_csv('data/eps30_data/eps_train_rd08.csv')\n```\nThis is another hard dependency on an external dataset path that is not accompanied by a data release in the provided code bundle. Since the paper’s claimed model accuracy and inverse-design demonstrations depend on the composition–property dataset collected across 162 aerogel types (plus augmentation), inability to access the exact data prevents reproduction of the reported metrics and plots. Moreover, without the raw experimental dataset, it is impossible to independently assess whether the held-out testing points (“never input into the model”) are truly independent with respect to the augmentation procedure and active-learning selection. In modern materials-ML practice, releasing the dataset and the deterministic training pipeline (including seeds, splits, and preprocessing) is standard for verifying conclusions. The current code package does not meet that bar, weakening the reproducibility of the paper’s core results.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|GPT|5", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "The manuscript’s conclusion that the system “automate[s] the inverse design … without the need for iterative optimization experiments” is not adequately justified because the inverse-design procedure is demonstrated on a small number of constraint queries using clustering heuristics, without benchmarking against standard sequential design/optimization baselines or reporting success rates across the feasible space.\n\n“Second, the inverse design of conductive aerogels was automated by the champion model, without the need for iterative optimization experiments. … By inputting these design requests, the champion model performed clustering analyses to pinpoint the most suitable sets of fabrication parameters.”\nThis describes an inverse-design method based on clustering in the predicted property space, followed by fabricating a small set of suggested recipes for two design requests. While this is a reasonable demonstration of using a surrogate model to propose candidates, it does not establish that the approach reliably satisfies arbitrary multi-property constraints across the design space or that it is more efficient than simpler baselines (e.g., random search within the feasible region). The phrase “without the need for iterative optimization experiments” is particularly strong given that the paper’s broader workflow already relies on iterative active-learning cycles to gather data and train the model; the inverse-design step is only “non-iterative” after substantial iterative data acquisition. The manuscript does not report a systematic success rate (fraction of proposals meeting constraints) over many independent target specifications, which is common when claiming automated inverse design. Consequently, the generality and strength of the inverse-design conclusion are not fully supported by the limited validation presented.\n“Fundamentally, Bayesian optimization is a sequential model-based approach to solving problem (1). … Equipped with this probabilistic model, we can sequentially induce acquisition functions … to guide exploration.” [[6]](#ref-6)\nThis describes a widely used paradigm for efficient materials/process optimization under expensive experiments: sequential, uncertainty-aware search guided by an acquisition function. The reviewed manuscript already uses an active-learning concept during data collection, but its inverse-design step is described as clustering-based selection rather than an explicit constrained optimization policy with uncertainty quantification. Without such a policy (or a comparison to one), it is hard to support the claim that iterative optimization experiments are unnecessary in general, especially when targets change or when constraints are tight and multi-objective. A standard expectation in the field is to evaluate design algorithms by the number of experiments needed to hit constraints or improve objective values relative to baselines, not just by showcasing a small set of successful recipes. Therefore, compared to common practice, the paper’s inverse-design evaluation is insufficiently comprehensive to warrant the broad conclusion.\n\nReferences:\n[6] <a id=\"ref-6\"></a> [Shahriari et al. “Taking the Human Out of the Loop: A Review of Bayesian Optimization” (Proc. IEEE, 2016)](https://lips.cs.princeton.edu/pdfs/shahriari2016loop.pdf)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "The paper employs a methodologically unsound approach of training a neural network on a small dataset (162 points) by artificially inflating it 1000-fold using Gaussian noise injection, which likely leads to overfitting and unreliable performance metrics.\n\n\"Through 8 active learning cycles with data augmentation, 162 kinds of conductive aerogels are fabricated/characterized... enabling the construction of an artificial neural network prediction model.\" (Abstract)\nThis statement confirms that the total number of unique experimental data points is only 162. Training a neural network, which typically requires large datasets to generalize effectively, on such a small sample size is highly prone to overfitting.\n```python\ndef augmente_data(raw_df, x_cols, y_cols, n_augmented=0,\n                  y_std_cols=None, x_std=0, y_std=0,\n                  id_col='sID', da_col='DA#', random_state=None):\n    ...\n    for i in range(n_augmented):\n        noisy_x = pd.DataFrame(rng.normal(raw_df[x_cols], x_std_df), columns=x_cols)\n        noisy_y = pd.DataFrame(rng.normal(raw_df[y_cols], y_std_df), columns=y_cols)\n```\nThe code demonstrates that data augmentation is performed by simply adding Gaussian noise to both the input features (`noisy_x`) and the target variables (`noisy_y`) of the existing data points. This process does not introduce new information about the underlying physical relationship but merely creates a cloud of points around the original samples.\n\"augmente_data(train_df, x_cols, y_cols, n_augmented=1000, x_std=0.05, y_std=0.05, random_state=0)\" (code/data_augmentation.ipynb)\nThe code shows that the dataset is augmented by a factor of 1000. Treating these 162,000 synthetic points as independent training samples for a neural network is statistically invalid. It forces the model to overfit to the noise distribution and the specific locations of the 162 original points, rather than learning the true material property landscape.\n\"Machine learning (ML) models... require large datasets for training... However, in materials science, data generation is often expensive and time-consuming.\" [1]\nThis reference highlights the known challenge of small datasets in materials science. Standard practice for small datasets involves using probabilistic models like Gaussian Processes or transfer learning, rather than artificially inflating data with noise to fit a high-capacity model like a neural network.\n\nReferences:\n[1] Butler, K. T., Davies, D. W., Cartwright, H., Isayev, O. & Walsh, A. Machine learning for molecular and materials science. Nature 559, 547–555 (2018). https://www.nature.com/articles/s41586-018-0337-2", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "The paper defines \"pressure sensitivity\" in a non-standard way that conflates the material's mechanical strength with its electrical response, leading to a misleading assessment of its performance as a strain-insensitive conductor.\n\n\"Pressure Sensitivity (\\( S \\)) = \\( \\frac{|(R - R_0)/R_0|}{\\sigma_{30}} \\) (4)\" (Main Text)\nThe authors define sensitivity by normalizing the relative resistance change by the compressive strength at 30% strain (\\( \\sigma_{30} \\)). This is physically inconsistent with the standard definition of sensitivity, which is the derivative of the signal with respect to the applied stimulus (pressure).\n\"Sensitivity was characterized by the following equation: S = (ΔC/C0)/ΔP\" [2]\nThis citation illustrates the standard definition of sensitivity for pressure sensors (capacitive or resistive), where the response is divided by the change in applied pressure (\\( \\Delta P \\)), not a material constant like strength.\n\"The model-suggested conductive aerogel exhibited... an ultralow pressure sensitivity of 0.02 kPa\\(^{-1}\\).\" (Main Text)\nBy dividing by \\( \\sigma_{30} \\), a material that is simply very strong (high \\( \\sigma_{30} \\)) will appear to have low \"sensitivity\" even if its resistance changes significantly. This metric fails to isolate the stability of the electrical network under deformation, which is the property of interest for \"strain-insensitive\" heating.\n\nReferences:\n[2] Xiong, Y. et al. Highly Sensitive Capacitive Pressure Sensor Based on a Flexible Microstructured Dielectric Layer. Sensors 20, 5134 (2020). https://www.mdpi.com/1424-8220/20/18/5134", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "The paper fails to compare the proposed Neural Network approach with simpler, more robust machine learning models suitable for small datasets, such as Gaussian Processes or Random Forests, to justify the complexity and the questionable data augmentation strategy.\n\n\"The AI/ML adoption in materials science research has surged... However, building a prediction model for conductive aerogels encounters significant challenges, primarily due to the lack of high-quality data points.\" (Introduction)\nThe authors acknowledge the small data problem but proceed to use a Neural Network with massive augmentation. They do not provide any comparison to show that this approach outperforms standard small-data techniques.\n\"Gaussian process regression (GPR) is a powerful tool for non-parametric regression... particularly useful for small datasets.\" [3]\nThis reference establishes Gaussian Processes as a standard and often superior baseline for small datasets in materials science, providing uncertainty estimates without the need for artificial data inflation. The absence of such a comparison weakens the claim that \"Machine Intelligence\" (specifically the chosen NN architecture) was necessary or effective.\n\nReferences:\n[3] Deringer, V. L. et al. Gaussian Process Regression for Materials and Molecules. Chemical Reviews 121, 10073–10141 (2021). https://pubs.acs.org/doi/10.1021/acs.chemrev.1c00022", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "Aerogels are materials with ultra-low density. What is the effect of density on the electrical properties? How do the densities of aerogels vary with grade A,B and C?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "Please list the descriptors used in the machine learning and explain the rationale.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "The fabrication parameters (as listed in Figure S5) include only the ratios/loading, which are related to the composition. Other fabrication parameters, such as temperatures, pressures, should be included.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "Page 6, paragraph 2. “Over 5300 data points are required, given a step size of 2.0wt% and four mixture loadings”. Please illustrate how the number of 5300 is calculated based on the step size of 2.0wt%.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "Page 9, in Fig. 1(b) and (c), which axis represents the amount of gelatin?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "Page 12, “Finally, the database contained approximately 160,000 data points”. Are the 160,000 data points employed in the prediction?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "Contextualization with recent work: Significant work has been published recently on automating experimentation in various contexts of materials development. The manuscript would benefit from summarizing these efforts, and comparing them with the proposed methods in terms of novelty, advantages, and potential disadvantages.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "Exploration of known correlations: In the introduction, the authors mention that correlations between the ingredients are “largely” unexplored, but do not elaborate on those that are explored. Providing more details on these known correlations and potentially incorporating them into their experimentation could increase efficiency.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "Comparison with traditional (experimental) approaches: The implementation of SHAP and FEA to elucidate the ML algorithm’s reasoning is well-founded. However, it would be beneficial if the authors provided more context on the advantages of this approach compared to traditional experimental methods, such as Design of Experiments (DoE), optimization methods, and experimentally validated finite element analysis (FEA) models, which might yield comparable results in potentially less time.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "Quantitative comparison with DoE: The authors briefly mention DoE in the conclusion, claiming greater efficiency for their approach. This assertion would be more compelling if supported by quantitative data, such as the number of experimental runs required by a DoE design to achieve a similar level of information and predictive capability.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "Writing improvements: Address minor grammatical issues, such as inconsistencies in parenthesis usage (e.g., “silk nanofibrils, chitosan”)”. Also, avoid repetitive language, like the repetition of ‘conductivity’ in the very first sentence. Some statements are vague, such as “Multiple blind tests were performed by different researchers to maintain unbiased evaluations.” Specifying the number of tests would provide clarity.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "Methodological details: Clarify how the freeze-drying process is automated, if at all. While there is some context in the Supporting Information, a brief mention in the main document would be beneficial.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "Clarification on testing procedures: The results suggest that conductivity was tested after compressive stress testing. It would be helpful if the authors clarified whether new samples were produced for each test or if the same samples were reused (Page 11).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "However, it is common to prepare both conductive and elastic aerogels by introducing elastic CNF and conductive MXene, many studies have explored MXene/CNF systems including their conductivity and compressibility. In this experiment, machine learning only replaced the feeding and matching process, but could not independently analyze the results to improve the formula. It may be far from people’s expectations to the significance of machine learning in related areas. Compared to previous reports, there is no enough novelty to ensure its publication in nature communications.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "MXene/CNF aerogels have been widely reported, and optimization schemes can be selected based on the establishment of conductive thresholds and elastic systems.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "Machine learning replaces the human formulation of different proportions of the mixture, the lack of a reasonable screening scheme - analysis - self-correction - the process of drawing conclusions.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "Why choose MXene/CNF system, how to solve the oxidation problem and the aggregation problem introduced by CNF of MXene?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|40|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb40", "comment": "There are some typos and grammar mistakes, the authors should be more careful.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Claude|1", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "The study relies on space-for-time substitution to make global projections about biodiversity changes from closing yield gaps and comparing intensification versus expansion scenarios, but this methodological approach has been shown to underestimate the magnitude of biodiversity-land use relationships, particularly in tropical forests, potentially biasing the study's conclusions about the relative impacts of different agricultural strategies.\n\n\"We use a space-for-time substitution to model three biodiversity metrics: sampled species richness, sampled total abundance, and relative community abundance-weighted average range-size (RCAR).\"\nThe authors explicitly acknowledge using space-for-time substitution as their core methodological approach. This method assumes that spatial variation can substitute for temporal variation, but published research has demonstrated that this assumption may systematically underestimate biodiversity losses associated with land-use change. The study then uses these spatially-derived models to project future temporal changes (closing yield gaps, comparing expansion vs. intensification scenarios), which extends the inference far beyond what the underlying spatial data can reliably support.\n\"Fifth, there are several limitations of using spatial biodiversity data to infer changes through time, most importantly an inability to consider time lags in biotic changes and responses to environmental changes (Wearn et al. 2012).\"\nWhile the authors acknowledge this limitation, they still proceed to make global projections about future biodiversity changes. The citation to Wearn et al. (2012) on extinction debt is relevant, but the implications for their projections are not fully addressed. The inability to account for extinction debt and time lags means that the projected losses could be substantially underestimated, particularly in the tropics where extinction debt may be substantial. This limitation is not merely a caveat but fundamentally affects the validity of comparing intensification vs. expansion scenarios.\n\"Critically, space-for-time methods underestimated the relationship between logging intensity and biodiversity losses, with changes in species richness twice as severe as estimated by space-for-time\" [[1]](#citation-1)\nFrança et al. (2016) demonstrated using a BACI (Before-After-Control-Impact) design that space-for-time substitution underestimated biodiversity losses by a factor of two compared to actual temporal measurements in tropical logged forests. If similar underestimation applies to agricultural intensification, the paper's conclusions about the relative merits of intensification versus expansion could be substantially biased. This is particularly concerning for the tropical results where the paper claims intensification leads to increased abundance and biotic homogenization.\n\nReferences:\n[1] França, F., Louzada, J., Korasaki, V., Griffiths, H., Silveira, J.M. & Barlow, J. (2016). Do space-for-time assessments underestimate the impacts of logging on tropical biodiversity? An Amazonian case study using dung beetles. *Journal of Applied Ecology*, 53, 1098-1105. https://besjournals.onlinelibrary.wiley.com/doi/full/10.1111/1365-2664.12657", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Claude|2", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "The study pairs biodiversity data sampled \"mostly from 2000 to 2012\" with yield data from \"around the year 2000,\" creating a temporal mismatch of up to 12 years where yield conditions at the time of biodiversity sampling may have differed substantially from the yield data used in the models, potentially confounding the yield-biodiversity relationships.\n\n\"For biodiversity data, we used the 2016 release of the PREDICTS database, which contains 3,250,404 biodiversity records, mostly sampled from 2000 to 2012, from 666 published studies (Hudson et al. 2017).\"\nThe biodiversity sampling spans a 12-year period, with \"most\" data collected after 2000 but the exact temporal distribution is not specified. Given that agricultural yields can change substantially over a decade due to technological improvements, management changes, and market forces, biodiversity sampled at a site in 2010 or 2012 may be responding to yield conditions quite different from the 2000 EarthStat estimates used in the analysis.\n\"EarthStat agricultural estimates include global estimates of yield and harvested areas for 175 crops in 206 countries around the year 2000 at a spatial resolution of 5' × 5' (~10 km × 10 km at equator) (Monfreda et al. 2008).\"\nThe yield data is fixed at year 2000, while biodiversity data spans 2000-2012. Ray et al. (2012), cited by the authors, documents substantial yield stagnation and changes during this period. If yields changed between 2000 and when biodiversity was actually sampled, the models would be relating current biodiversity to historical yields, not the yields that actually shaped the observed communities. This temporal mismatch is particularly problematic for the projections, which assume the 2000 yield-biodiversity relationship will hold when extrapolating to yield gap closure scenarios.\n\"As a consequence, our results are most representative of the time window represented by the EathStat and PREDICTS data, which is the time period between 2000 and 2005.\"\nThe authors claim representativeness for 2000-2005, yet the PREDICTS data extends to 2012 and \"most\" data was sampled after 2000. This statement appears to conflate the yield data reference period (2000) with the broader PREDICTS sampling window without providing evidence that the majority of biodiversity samples were collected between 2000 and 2005. Without knowing the actual temporal distribution of the PREDICTS samples used, the extent of this mismatch cannot be properly assessed.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Claude|3", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "The study matches local biodiversity samples (with maximum linear spans of 3-502 meters for most PREDICTS sites) with landscape-scale yield estimates at ~10 km × 10 km resolution, and acknowledges that cropland sites may not be sampling within areas cultivated with the specific crops for which yields are estimated, creating a fundamental scale mismatch that weakens causal inference about yield impacts on biodiversity.\n\n\"Second, our cropland data were not sampled necessarily within cropland cultivated with the particular crops for which we are using landscape-scale yield estimates. Therefore, our models capture landscape-scale but not local-scale impacts of crop-specific management.\"\nThis is a significant acknowledgment that the biodiversity data may not be directly influenced by the crop yields used in the models. If a biodiversity sample was collected in a wheat field but the dominant crop in the 10×10 km grid cell is maize, the local biodiversity would be driven by wheat management while being modeled against maize yield. This mismatch fundamentally undermines the claim that the models capture the causal relationship between crop-specific yield increases and biodiversity outcomes.\n\"Sampling at the sites in PREDICTS can span a range of different spatial extents. The maximum linear span of sampling for three-quarters of sites in the PREDICTS database falls between 3 and 502 metres.\" [[2]](#citation-2)\nThe PREDICTS sampling sites are typically orders of magnitude smaller than the 10 km × 10 km yield data resolution. This creates an ecological scaling problem where local community metrics (species richness, abundance) are being related to landscape-average yield values that may not reflect conditions at the sampling location. Heterogeneity within a 10×10 km cell in terms of crop types, management intensity, and natural vegetation could be substantial, particularly in tropical regions with smallholder agriculture.\n\"For our purposes, we define landscape scale as the extent of one raster cells in our spatial data.\"\nThis operational definition conflates the scale of available yield data with a meaningful ecological landscape scale. The assumption that a ~100 km² grid cell represents a coherent \"agricultural landscape\" for modeling biodiversity responses ignores the substantial within-cell heterogeneity that exists in most agricultural regions. This scale choice appears to be driven by data availability rather than ecological rationale.\n\nReferences:\n[2] Hudson, L.N., Newbold, T., Contu, S., et al. (2017). The database of the PREDICTS (Projecting Responses of Ecological Diversity In Changing Terrestrial Systems) project. *Ecology and Evolution*, 7, 145-188. https://onlinelibrary.wiley.com/doi/10.1002/ece3.2579", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Claude|5", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "The study's estimates of biodiversity loss from closing yield gaps (maximum 89.1% species loss, 99.7% abundance loss) are dramatically higher than those from Kehoe et al. (2017) (maximum 7% species richness loss, 13% abundance loss), a ~10-fold difference that the authors attribute to model complexity but that warrants more rigorous validation or reconciliation given both studies use the same underlying PREDICTS dataset.\n\n\"Kehoe et al. (2017), who analyse the biodiversity impact of maximising agricultural intensity on all existing farmland, estimate a maximum of 7% loss in species richness, which contrasts with our maximum of 89.1% species loss, and 13% loss is abundance, which contrasts with our maximum 99.7% loss in abundance from closing yield gaps.\"\nA 10-fold difference in estimated maximum biodiversity loss between studies using the same underlying biodiversity database is striking. While methodological differences exist (the current study includes crop-specific models and interactions with biome type and natural habitat), such dramatic discrepancies suggest that the estimates are highly sensitive to model specification. Without independent validation data, it is difficult to assess which estimate is more accurate, and readers should be cautious about accepting the larger estimates without additional corroboration.\n\"The difference in results is likely due to the focus of Newbold et al. (2015) on agriculture in general rather than crop type, and absence of interactions between intensity, and natural habitat or biome type in their statistical models (Newbold et al. 2015).\"\nThe authors attribute the discrepancy to model complexity (adding interactions), but adding complexity to statistical models does not necessarily make them more accurate—it can also amplify noise, especially with weak underlying relationships (as evidenced by low marginal R²). The claim that interactions \"obscured\" negative impacts in simpler models implies that the larger estimates from complex models are correct, but this is an assumption that requires validation against independent data.\n\"Finally, some of our more models were less robust to the choice of yield data source (Table S9) and their results should be interpreted with caution.\"\nThe acknowledgment that some models are not robust to data source choice is concerning for results claiming ~90% biodiversity losses. Model sensitivity to input data suggests that the large estimates may be driven by data quirks or model specification rather than true ecological patterns. The specific mention of rice-total abundance and maize-RCAR models not agreeing on direction of effects between EarthStat and MapSPAM indicates substantial methodological uncertainty that propagates into the global projections.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|GPT|1", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "This paper draws quantitatively strong conclusions about the biodiversity consequences of increasing yields and “closing yield gaps” from cross-sectional spatial associations, which is insufficient for causal or temporal interpretation and undermines the validity and reliability of the projected magnitudes.\n\n“We use a space-for-time substitution to model three biodiversity metrics: sampled species richness, sampled total abundance, and relative community abundance-weighted average range-size (RCAR).”\nThis sentence states that the core identification strategy is space-for-time substitution rather than observing biodiversity before/after yield changes within the same locations. In practice, yield is entangled with many spatially structured factors (e.g., long-run land-use history, soil, irrigation, market access, governance, and unmeasured management inputs), so spatial correlations between yield and biodiversity can differ from within-place changes over time. The paper does include some covariates (e.g., climate, human-occupation history), but that does not guarantee the remaining confounding is negligible, especially at global scale and 10 km pixels. Because the main outputs are framed as percentage losses from “closing yield gaps,” readers can easily interpret these as expected consequences of interventions, which space-for-time alone cannot justify. This gap matters most for the headline figures and policy-relevant statements about intensification versus expansion.\n“For the yield-biodiversity models, we used global agricultural estimates based on national and sub-national statistics whose spatial allocation to pixel level was modelled following certain assumptions.”\nThis sentence acknowledges that the yield predictors are not directly observed at each biodiversity sampling site but are modelled, downscaled surfaces. Such products can be useful, but they add a second layer of potential mismatch between the true local management experienced by organisms and the covariate used in the regression. When combined with space-for-time substitution, any spatial artefacts or systematic errors in the yield surfaces can translate into biased biodiversity–yield relationships. This is particularly important because the paper’s projections are computed by applying these estimated relationships across all global pixels for scenario maps. In other words, uncertainty and bias in the exposure variable (yield) are amplified through extrapolation. Common practice in global-change inference is to be explicit that such results are correlational and to test transferability assumptions; the paper does not provide a strong validation that spatial yield–biodiversity slopes represent temporal responses to yield increases.\n“When closing yield gaps for all four crops, as estimated for the year 2000, 83% of all grid cells would experience a decrease in species richness. Mean species richness change per pixel globally was −11.8% and the median was −10.8%.”\nThese are precise, global percentage-loss estimates that will likely be read as expected consequences of an intensification pathway. However, the projection inherits the limitations of space-for-time substitution and exposure measurement discussed above, so the magnitude (e.g., −10.8% median richness) is not robustly supported as a causal effect of yield-gap closure. The sentence also illustrates that the paper emphasizes distribution-wide summaries (percent of grid cells, mean/median changes) without demonstrating that the underlying relationships are stable under intervention-like changes. In intervention contexts, yield-gap closure typically implies changes in inputs and practices that can decouple yield from biodiversity in ways not represented in the historical cross-section. Without stronger causal identification or temporal validation, these global summary numbers should be treated as scenario-sensitive associations rather than reliable effect estimates.\n“We find that SFTS methods share common limitations relating to (i) the causality of identified spatial climate-biotic relationships and (ii) the transferability of these relationships, i.e. whether climate-biotic relationships observed over space are equivalent to those occurring over time.” ([1](https://ecoevorxiv.org/repository/view/4688/))\nThis quote summarizes two central reasons space-for-time substitution can fail: the spatial relationship may not be causal, and even if causal, it may not transfer to temporal change. The paper under review uses SFT logic to interpret yield–biodiversity patterns as consequences of yield increases and yield-gap closure, which requires precisely these assumptions. The authors partially acknowledge related concerns in their limitations, but the main results still present strong quantitative projections. In fields using SFT, a standard mitigation is to explicitly test transferability or validate with independent temporal data when possible. The reviewed paper does not provide such validation for yield increases, making the causal reading of the projections substantially weaker.\n“Perret et al. show that the space-for-time gambit yields dramatically flawed estimates of a species’ temporal responses to climatic variation and climate change.” ([2](https://pmc.ncbi.nlm.nih.gov/articles/PMC10823171/))\nThis quote provides a concrete, recent demonstration that space-for-time can produce large and even sign-wrong errors when predicting temporal responses. While that study is about climate–growth responses, the methodological warning generalizes: spatial gradients need not reproduce temporal dynamics. The reviewed paper similarly extrapolates from spatial gradients in yield to infer temporal impacts of raising yields, including large, policy-relevant percentage changes. Given that the paper’s main claims depend on SFT validity at global scale, the possibility of dramatic error is not a minor caveat; it directly affects whether the projected biodiversity losses can be trusted. This makes the paper’s conclusions about the costs of closing yield gaps substantially less secure than the presented numbers suggest.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|GPT|2", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "This paper relies on backward stepwise fixed-effects selection using likelihood-ratio-test p-value thresholds in multi-interaction mixed models, a procedure known to inflate false positives and bias effect sizes, which threatens the validity of the selected yield–biodiversity relationships and downstream global projections.\n\n“We performed backward stepwise selection based on likelihood-ratio tests with a p-value threshold of 0.05 to select the fixed-effects structure for each model.”\nThis sentence shows that the main model structures are chosen via stepwise null-hypothesis testing rather than a pre-registered hypothesis set or a principled model-comparison framework accounting for selection uncertainty. Because the paper considers many candidate variables and multiple interactions, repeated testing can substantially increase the probability of selecting spurious terms. The resulting “best” model can then yield overconfident coefficients and exaggerated effect sizes, especially when selection is followed by standard inference as if the model were fixed a priori. This is particularly consequential here because the models are used for global scenario projections (yield-gap closure and 1% production-change comparisons), so any selection-induced bias is propagated to maps and headline statistics. The paper acknowledges some convergence issues and robustness checks, but those do not address the core statistical invalidity of stepwise p-value-based selection for inference.\n```r\n    print(paste(length(which(pVals > 0.05)), \" interaction terms have P-values >0.05\", \n                sep = \"\"))\n    if (length(which(pVals > 0.05)) == 0) \n      break\n    dropI <- iTerms[order(pVals)[length(order(pVals))]]\n    stats$ChiSq[which(stats$terms == dropI)] <- Chis[order(pVals)[length(order(pVals))]]\n    stats$Df[which(stats$terms == dropI)] <- Dfs[order(pVals)[length(order(pVals))]]\n    stats$P[which(stats$terms == dropI)] <- pVals[order(pVals)[length(order(pVals))]]\n    stats$dAIC[which(stats$terms == dropI)] <- dAICs[order(pVals)[length(order(pVals))]]\n    print(paste(\"Dropping \", dropI, sep = \"\"))\n    t1 <- gsub(\"[(]\", \"[(]\", dropI)\n    t2 <- gsub(\"[)]\", \"[)]\", t1)\n    t3 <- paste(t2, \"[+]\", sep = \"\")\n    call.old <- gsub(t3, \"\", call.old)\n    iTerms <- iTerms[-order(pVals)[length(order(pVals))]]\n    allTerms <- allTerms[-which(allTerms == dropI)]\n    iter <- iter + 1\n```\nThis code (GLMERSelect_TMB) operationalizes the stepwise procedure by iteratively dropping interaction terms with non-significant LRT p-values. Iterative testing and term removal is exactly the workflow that creates “cryptic multiple testing,” because many hypotheses are tested without an explicit error-rate adjustment. The choice of which term to drop is driven by p-values rather than by an analysis plan tied to mechanistic hypotheses, increasing the risk of selecting unstable models that do not generalize. The code also shows that the procedure is applied automatically, making it difficult to trace which modeling decisions are data-driven versus theory-driven. Given that the paper’s key claims depend on which interactions survive this selection, this implementation raises a serious risk that reported interaction patterns (e.g., yield × biome, yield × natural habitat) are artifacts of the selection process.\n“The principal drawbacks of stepwise multiple regression include bias in parameter estimation, inconsistencies among model selection algorithms, an inherent (but often overlooked) problem of multiple hypothesis testing, and an inappropriate focus or reliance on a single best model.” ([4](https://pubmed.ncbi.nlm.nih.gov/16922854/))\nThis quote concisely enumerates the specific statistical problems that apply to the modeling approach used in the reviewed paper. The reviewed paper uses stepwise selection to pick a single final model per crop and biodiversity metric, then treats that model as the basis for projections and interpretations. Bias in parameter estimation is particularly damaging when effect sizes are later transformed into percentage losses and used for mapping. The multiple-testing problem is acute because the paper includes multiple predictors and several interactions, so “significant” effects can appear even under weak true signals. The reliance on a single selected model also ignores model-selection uncertainty, which is important for robust inference and should be reflected in uncertainty estimates for projections.\n“These analyses clearly demonstrate that significance tests based on stepwise procedures lead to greatly inflated Type I error rates (i.e., the probability of erroneously rejecting a true null-hypothesis).” ([3](https://dash.harvard.edu/bitstream/handle/1/5344225/Mundry%20and%20Nunn.pdf?sequence=1))\nThis statement directly identifies the central inferential failure mode of stepwise p-value selection: inflated false positives. Because the reviewed paper uses LRT p-values as the selection criterion, the selected interactions and main effects are more likely to include chance findings than their nominal p-values suggest. This matters for both the direction and magnitude of yield effects, and for whether yield is deemed important at all for a given crop–metric combination. In global projections, even small spurious slopes can accumulate into large mapped differences when applied across many pixels. The paper’s robustness checks (negative binomial and Bayesian refits) do not eliminate the selection-induced Type I error inflation unless model selection itself is addressed.\n“Stepwise deletion procedures have come under heavy criticism; they can overestimate the effect size of significant predictors (Whittingham et al., 2006; Forstmeier & Schielzeth, 2011; Burnham, Anderson & Huyvaert, 2011) and force the researcher to focus on a single best model as if it were the only combination of predictors with support in the data.” ([5](https://pmc.ncbi.nlm.nih.gov/articles/PMC5970551/))\nThis sentence summarizes two well-documented pathologies of stepwise deletion: effect-size exaggeration among retained predictors and an artificial focus on a single selected model. Both matter here because the paper translates fitted slopes into percent biodiversity changes and maps them globally, so any effect-size inflation directly scales the projected losses. The reliance on a single “best” selected model per crop/metric also ignores the presence of many near-equivalent models, meaning reported interaction patterns may be unstable across small perturbations. This is especially relevant given the paper’s admitted convergence issues and low marginal pseudo-R², which suggest weak fixed-effect signal relative to random-effects variability. Consequently, the apparent strength of yield effects (and interactions) may be overstated, and the maps should be interpreted as highly model-dependent.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|GPT|3", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "This paper reports global scenario results (yield-gap closure and 1% production-change comparisons) as precise percentages and mapped outcomes without propagating statistical uncertainty, even though it acknowledges that model diagnostics indicate assumption violations; this undermines the robustness of the magnitude and spatial patterns of the conclusions.\n\n“The model diagnostic plots suggest that our models do not fully fit model assumptions (Figure S5 – S21).”\nThis sentence concedes that the fitted models do not adequately satisfy their assumptions, which is a serious concern because the models are used to generate quantitative projections and scenario comparisons. When assumptions are violated (e.g., distributional form, residual structure, overdispersion handling), coefficient estimates and predictions can be biased, and standard errors and confidence intervals can be unreliable. The paper notes that alternative distributions did not “substantially improve model behaviour,” which suggests persistent misspecification rather than a minor issue. Nonetheless, the results are still summarized with strong global statements (e.g., percent of grid cells losing richness; large median losses) that implicitly rely on model adequacy. In a projection-driven paper, acknowledged model inadequacy should trigger either reformulation of models or much more cautious interpretation with explicit uncertainty characterization.\n“Mean species richness change per pixel globally was −11.8% and the median was −10.8%.”\nThis result reports a highly specific global effect size, but it is presented without an uncertainty interval that accounts for model-parameter uncertainty, selection uncertainty, and exposure-layer uncertainty. Given the admitted diagnostic problems, point estimates can be misleading because small changes in model form or coefficient values may meaningfully change medians and affected-area percentages. Moreover, because the projections are obtained by applying model predictions to every pixel, uncertainty should ideally be mapped or summarized (e.g., via posterior predictive simulations or bootstrap resampling). Without this, readers cannot assess whether differences between regions (or between intensification vs expansion) are statistically meaningful or within plausible error bounds. The precision of the reported numbers therefore overstates the strength of evidence.\n```r\n  for(z in 1:length(dat)){\n    if(logLink == \"e\"){\n      new_dat <-exp(predict(mod, newdata = dat[[z]], re.form = ~ 0, type = \"response\"))\n    } else{\n      if(logLink == \"10\"){\n        new_dat <-10^(predict(mod, newdata = dat[[z]], re.form = ~ 0, type = \"response\"))\n      } else {\n      new_dat <-predict(mod, newdata = dat[[z]], re.form = ~ 0, type = \"response\")\n      }\n    }\n    new_dat_df <-data.frame(x = dat[[z]]$x, \n                            y = dat[[z]]$y, \n                            Ha = dat[[z]][,paste0(crop_name, \"_HarvestedAreaHectares\")],\n                            RelFractions = dat[[z]]$relativeFractions,\n                            perNat = dat[[z]]$per_nat_resampled,\n                            CroplandPer = dat[[z]]$cropland_per_resampled, \n                            primVegPer = dat[[z]]$primVeg_per_resampled,\n                            areas = dat[[z]]$areas,\n                            area_ha = dat[[z]]$areas_ha,\n                            BiodivPred = new_dat)\n```\nThis code (PredictFunc in 00a_Functions.R) shows that projections are generated as deterministic fitted values from `predict(...)`, with no simulation-based uncertainty propagation. There is no resampling of coefficients, no posterior draws, and no use of prediction intervals even though the paper also runs Bayesian versions of models. As a result, the scenario maps and summary percentages are effectively single “best-guess” surfaces, not distributions of possible outcomes. In global policy-relevant projections, it is common to report uncertainty bands or credible intervals, particularly when models are later combined with other spatial layers. The absence of this step is especially problematic given the paper’s own statement that model assumptions are not fully met.\n“We strongly encourage researchers to view model fit and model adequacy as two separate but equally important traits that must be assessed and reported.” ([5](https://pmc.ncbi.nlm.nih.gov/articles/PMC5970551/))\nThis guidance is particularly salient because the reviewed paper acknowledges assumption violations yet proceeds to report precise global percentage changes and scenario maps. When adequacy is questionable, point predictions can be systematically biased in some covariate regimes, and the direction of error may differ across regions. In such cases, best practice is to either improve the model until adequacy is acceptable or to explicitly represent the resulting uncertainty in projections. The reviewed paper does not provide uncertainty ranges for its mapped outcomes or medians that incorporate parameter uncertainty and model-selection uncertainty. This makes it difficult to judge whether spatial contrasts (e.g., tropics vs non-tropics, expansion vs intensification) are robust or within plausible error.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|GPT|4", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "This paper’s RCAR metric (used to infer biotic homogenisation and a key tropical-impact conclusion) relies on GBIF occurrence-derived area-of-occupancy estimates, but GBIF data are known to have large geographic biases and biodiversity-hotspot gaps, which can bias range-size proxies and threaten the validity of the paper’s homogenisation conclusions.\n\n“We used a RCAR metric as calculated in Newbold et al (2018) based on occurrence data from the GBIF database (GBIF.org 2015). The estimated area of occupancy of each species, computed as the sum of the total area of grid cells containing GBIF records of the respective species, was extracted at 55 km × 55 km resolution.”\nThis description makes clear that the range-size proxy is derived from the footprint of GBIF occurrences on a fixed grid, not from comprehensive atlas data or model-based occupancy that explicitly accounts for sampling effort. Area of occupancy estimated from presence records is sensitive to where observers and institutions collect and digitize records, which is uneven across regions and taxa. This is not a minor technicality because RCAR is interpreted as “biotic homogenisation,” and the paper reports strong spatial patterns (including a large tropical signal). If occurrence density is lower in certain high-biodiversity regions, species can appear artificially narrow-ranged, changing community-average range-size calculations. That can change both baseline RCAR and the estimated direction/magnitude of RCAR shifts with yield, especially when analyses compare tropical vs non-tropical regions.\n“Additionally, 30% of global agricultural landscapes, predominantly in the tropics, are likely to experience increased biotic homogenization.”\nThis is a major, policy-relevant claim that depends directly on RCAR being a reliable and comparably measured proxy across regions. The phrase “predominantly in the tropics” is exactly where GBIF data limitations are most likely to matter because many tropical regions and biodiversity hotspots are systematically under-sampled in digitized occurrence records. If RCAR is biased by spatial data gaps, the estimated fraction (30%) and its concentration in the tropics may be substantially misestimated. Because the paper treats RCAR increases as negative biodiversity outcomes, any bias that inflates RCAR changes in the tropics would directly strengthen the paper’s most alarming conclusion. Given this dependence, the paper should demonstrate that RCAR patterns are robust to GBIF sampling bias (e.g., sensitivity to record-density thresholds or alternative range-size sources), but such a robustness test is not provided in the main text.\n“A user will encounter many biases and gaps in these data which should be understood before data are used or analyzed. The data are notably deficient in many of the world's biodiversity hotspots.” ([6](https://pmc.ncbi.nlm.nih.gov/articles/PMC2043490/))\nThis quote provides direct evidence that GBIF data are not uniformly representative globally and that hotspot regions—often tropical—are particularly deficient. That deficiency matters for any metric that uses GBIF points to estimate range size or occupancy, including the RCAR pipeline described in the reviewed paper. Because hotspots often contain many narrow-ranged species, missing data can create systematic distortions in estimated range-size distributions. The warning also explicitly links the problem to downstream analysis: biases and gaps must be understood before using the data. The reviewed paper does not demonstrate that its RCAR-based homogenisation conclusions account for or are insensitive to these known gaps.\n“GBIF data for Legumes are a geographically biased sample. Large parts of the globe, including hotspots of biodiversity in Africa and Asia, are data deficient.” ([6](https://pmc.ncbi.nlm.nih.gov/articles/PMC2043490/))\nThis quote strengthens the concern by pointing to specific under-covered regions (Africa and Asia) that overlap with the paper’s focus on strong tropical patterns. Even if RCAR is computed for many taxa, this example shows that geographic bias is large enough to make GBIF-derived distributions non-global in practice. When area of occupancy is computed as the set of occupied grid cells, missing records reduce estimated occupancy, potentially misclassifying widespread species as narrower-ranged in under-sampled regions and altering community averages. Such distortions can be spatially patterned and could align with the paper’s tropical/non-tropical comparison, biasing effect estimates. Therefore, the paper’s inference that tropical landscapes are especially prone to homogenisation under yield increases is less secure than the paper presents.\n“Moreover, although open access primary biodiversity data are heterogeneous, resulting from the good will of contributors and not from a well-planned sampling protocol, they reflect our knowledge and practices in the study of biodiversity.” ([7](https://hal.sorbonne-universite.fr/hal-01585590v1/file/s41598-017-09084-6.pdf))\nThis quote emphasizes that open occurrence compilations like GBIF are not collected under a designed sampling scheme, which is precisely the condition that makes naive occupancy-from-records potentially biased. For RCAR, using GBIF grid-cell presence as “area of occupancy” assumes that sampling intensity does not systematically vary in a way that changes relative range-size estimates across taxa and regions. In reality, digitization, observer effort, and accessibility are structured geographically, so heterogeneity in data generation can leak into ecological metrics. The reviewed paper treats RCAR as a robust proxy for homogenisation, but without explicitly addressing these data-generation biases, the proxy may inherit them. That makes RCAR-based claims about where homogenisation risk is highest (and how it changes with yield) substantially more uncertain.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|GPT|5", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "This paper makes crop-specific claims (separate maize/soy/wheat/rice yield–biodiversity relationships and crop-specific expansion-vs-intensification comparisons) even though the underlying “cropland” biodiversity observations are not necessarily from the focal crop and require a strong, unvalidated assumption about similarity of intensification across cropping systems.\n\n“The PREDICTS cropland classification does not differentiate according to the crop cultivated at the precise sampling location. Therefore, the biodiversity data were sampled in landscapes used to grow the focal crops (according to EarthStat estimates), even if the actual sample may have been taken in a different crop. In doing so, we assume that intensification levels tend to be similar across cropping systems within an agricultural landscape.”\nThis is a key methodological assumption: the crop-specific exposure (yield for a particular crop) is linked to biodiversity observations that may come from a different crop at the sampled point. Because biodiversity responses can differ substantially across crops due to distinct management regimes, phenology, and habitat structure, the assumption of similar intensification across cropping systems is strong. If the assumption fails, estimated differences among crops (e.g., maize vs rice patterns) may partly reflect mismatches between the focal crop yield surface and the actual local land use. The paper then uses these crop-specific models in scenario comparisons, so any mismatch can propagate into maps and conclusions about whether intensification or expansion is “better” for each crop. The paper acknowledges this issue in limitations but still presents crop-disaggregated results as central outputs.\n“Second, our cropland data were not sampled necessarily within cropland cultivated with the particular crops for which we are using landscape-scale yield estimates. Therefore, our models capture landscape-scale but not local-scale impacts of crop-specific management.”\nThis limitation is not merely about finer spatial detail; it directly constrains the meaning of the crop-specific conclusions. If the models capture only landscape-scale associations, then interpreting them as impacts of management tied to a particular crop is precarious, especially when the paper compares crops and maps crop-specific outcomes. Moreover, the scenario exercise compares strategies “for each crop,” which implicitly assumes that changing that crop’s yield or area drives the local biodiversity outcomes the model predicts. Without crop-verified site-level land use (or at least stronger validation that landscape crop composition predicts local management), the crop-specific differences may not be attributable to the crops themselves. This reduces confidence in the paper’s claim that biome, crop, and natural vegetation jointly dictate whether intensification or expansion is worse.\n“Here, we provide a large-scale assessment of the biodiversity consequences of yield increases and land conversion in landscapes producing four crops (maize, soybean, wheat and rice).”\nThis framing signals that the paper’s central contribution is crop-specific, implying that results differ meaningfully among maize/soy/wheat/rice landscapes. Given the non-crop-specific nature of the cropland biodiversity sampling, the crop-specificity is primarily imposed via spatial intersection with crop-yield layers rather than by observing biodiversity in fields of each crop. That design can be informative about landscape contexts where these crops are grown, but it is weaker for attributing biodiversity changes to the crops’ own yield dynamics or management. Because the paper’s abstract and figures present crop-separated results prominently, readers may interpret these as crop-management impacts rather than landscape associations correlated with crop production. The evidence in Methods and Limitations shows that such an interpretation is not strongly supported.\n“Selection of crop types – defined as major categories of intensively-grown domesticated plants – and related management and production cycles determine the intensity of agricultural management.” ([8](https://pmc.ncbi.nlm.nih.gov/articles/PMC7241271/))\nThis quote supports the field’s expectation that crop identity and associated cycles materially influence management intensity, meaning that assuming similar intensification across cropping systems is risky. If crop types determine management intensity, then biodiversity sampled in “cropland” of an unspecified crop cannot be treated as interchangeable with the focal crop’s management conditions. This is especially important for a paper attempting to compare biodiversity impacts across specific crops. The reviewed paper’s approach could still be valuable for describing biodiversity correlates of crop-producing landscapes, but the crop-specific causal interpretation is weakened. Therefore, the crop-disaggregated scenario conclusions should be presented more cautiously and ideally supported with validation using crop-resolved land-use data at sampling locations.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "The projection of biodiversity impacts for intensification is methodologically inconsistent with the expansion scenario and contradicts the authors' claim that their models capture landscape-scale impacts. Specifically, the intensification projection weights the biodiversity change by the crop's relative area fraction, effectively treating the impact as local to the crop's footprint, whereas the models (based on generic \"Cropland\" data and landscape-scale yields) and the expansion scenario imply landscape-wide effects. This likely underestimates the biodiversity cost of intensification.\n\n\"Therefore, our models capture landscape-scale but not local-scale impacts of crop-specific management.\"\nThe authors explicitly state that their models capture landscape-scale impacts, implying that the yield variable (measured at ~10km resolution) influences biodiversity across the landscape (or at least across all cropland in the landscape), not just within the specific crop's fields.\n`MaizeSR$SR_1perIntensification_maize <- MaizeSR$PV_1perIntensification_RelFractions_maize * ((MaizeSR$PV_1perIntensification_BiodivPred_maize * MaizeSR$PV_1perIntensification_primVegPer_maize) + (MaizeSR$CL_1perIntensification_BiodivPred_maize * MaizeSR$CL_1perIntensification_CroplandPer_maize)) + (1-MaizeSR$PV_1perIntensification_RelFractions_maize) * MaizeSR$SR_noChange_maize`\nIn the code for intensification, the new biodiversity state (calculated using the increased yield) is weighted by `RelFractions` (the crop's share of agricultural area), while the remaining portion of the pixel is assumed to stay at the \"No Change\" state. This weighting treats the effect of increased yield as being confined to the specific crop's area, which contradicts the \"landscape-scale\" interpretation of the model. If the model predicts landscape-scale biodiversity based on landscape-scale yield, increasing the yield should affect the entire relevant land use (e.g., all cropland), not just a fraction.\n`MaizeSR$SR_1perExpansion_maize <- (MaizeSR$PV_1perExpansion_BiodivPred_maize * MaizeSR$PV_1perExpansion_primVegPer_maize) + (MaizeSR$CL_1perExpansion_BiodivPred_maize * MaizeSR$CL_1perExpansion_CroplandPer_maize)`\nIn contrast, the expansion scenario calculates the new biodiversity state for the entire pixel (based on new land use proportions) without any such weighting by the crop's relative fraction. This inconsistency biases the comparison in favor of intensification by dampening its estimated impact.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "The study relies on coarse-resolution (~10km) yield estimates to predict site-level biodiversity, ignoring local management intensity which is a critical driver of biodiversity. This \"ecological fallacy\" likely introduces substantial noise and bias, especially given that the authors explicitly discarded the available local-scale intensity data in PREDICTS.\n\n\"For our purposes, we selected only those sites located in cropland... or primary vegetation...\".\nThe authors filtered the PREDICTS database to include only \"Cropland\" and \"Primary Vegetation\" sites, discarding the \"Use Intensity\" (Minimal, Light, Intense) classification available in PREDICTS. By doing so, they threw away the only direct measure of local management intensity.\n\"EarthStat agricultural estimates... spatial resolution of 5’ × 5’ (~10 km × 10 km)\".\nThey replaced the local intensity measure with EarthStat yield data, which is aggregated at a ~10km scale. A 10km grid cell can contain a heterogeneous mix of intensive and extensive farms. Assigning the average yield of the grid cell to a specific biodiversity sampling site (which might be a low-intensity hedgerow or a high-intensity monoculture) introduces a severe scale mismatch.\n\"Errors in these estimates caused by the simplified landscape representation can originate from scaling errors (the 'ecological fallacy')\" [2]\nAs noted in the literature, inferring local relationships (biodiversity at a site) from aggregate data (landscape yield) is prone to the ecological fallacy. A site with high biodiversity might exist in a high-yield landscape (e.g., a refuge), leading the model to falsely associate high yield with high biodiversity, or vice versa.\n\nReferences:\n[2] Verburg, P. H., et al. (2013). The representation of landscapes in global scale assessments of environmental change. *Landscape Ecology*, 28, 1067-1080. https://doi.org/10.1007/s10980-012-9745-0", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "The definition of \"intensification\" is limited to yield increases per harvested area, thereby neglecting increases in cropping frequency (multiple cropping) which is a major pathway of agricultural intensification with distinct biodiversity impacts.\n\n\"For the intensification scenario, the only variable that changed was the yield for each crop\".\nThe authors simulate intensification solely by increasing the \"Yield per Hectare\" variable. In the EarthStat dataset, this variable typically represents production per *harvested* hectare.\n\"Harvesting currently single cropped areas a second time could increase global harvested areas by 87–395 million hectares\" [1]\nAgricultural intensification often involves increasing the number of harvests per year (multiple cropping), which increases annual production per physical hectare without necessarily increasing the yield per harvest. This form of intensification drastically reduces fallow periods and increases disturbance frequency, which can have severe negative impacts on biodiversity. By focusing only on yield per harvest, the study misses a critical dimension of intensification, potentially underestimating its biodiversity costs.\n\nReferences:\n[1] Waha, K., et al. (2020). Multiple cropping systems of the world and the potential for increasing cropping intensity. *Global Environmental Change*, 64, 102148. https://doi.org/10.1016/j.gloenvcha.2020.102148", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "The authors effectively delineate and explain the problem in the abstract and introduction, although there is a need for clear definitions of some terminology. For example, total “total abundance” is mentioned in lines 21 and 72-73, but it is not given an example of what it is how it measured (number of individuals, total biomass?; see also below the comment about lines 128-130, 18 and 118-119 below).", "reviewer_type": "human", "label": "error", "error_type": "Neglect", "label_origin": "expert+llm-filter"}
{"id": "prb|41|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "The Methods subsections are somewhat tedious and lengthy. I understand the importance of these sections, and I commend the authors for providing a very detail information. However, as it stands, it disrupts the flow of the article; this could be improved by using tables and moving some of the more detailed aspects to the Supplementary Material.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "How much of the conclusions can be generalized, given that only the impact of four crop types were assessed? While the authors provide a thorough discussion on the limitations of their approach, I did not see how they address this specific concern.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "I am rather surprised by the simultaneous use of frequentist and Bayesian statistics. This seems excessive and suggests a lack of confidence in one or both approaches.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "In line 642, under the section “Biodiversity impact of closing yield gaps” and in figure 4, I found the opposite effects on total abundance (figure 4b) and RCAR in the tropics (figure 4c) rather striking. Additionally, the contrasting effects between species richness and abundance (figures 4a, 4b) and RCAR (figure 4c) for non-tropical regions are noteworthy. I do not think these aspects are sufficiently highlighted in the text.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Line 18 - “Closing yield gaps”: If the authors want to reach a wide readership, including those unfamiliar with some of the terminology used in this field, they should provide a clear explanation of the meaning of several terms used, such as, “closing yield gaps.” Although it may seem obvious, it is easy to misunderstand its meaning.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Line 78: What is a “more ecological community”?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Line 84: Why ‘maize, soybean, wheat, and rice’ crops? The answer is on lines 185-186, but I would move it to the introduction.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_1|9", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Line 115: It is mentioned “6 predominant land-use classes.” Which ones?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_1|10", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Lines 118-119: The definition of “primary vegetation” only appears here, but it has been mentioned before. I suggest moving it to the location where it first appears.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_1|11", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Lines 128-130: It would be important to have some examples of measures of abundance.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_1|12", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Line 270: The authors use “subsistence yields” as a proxy for “agricultural suitability.” The rationale seems to be that the former does not require “inputs, irrigation, and most human management.” If I understand correctly, this seems to be a rather narrow definition of “subsistence yields,” because even subsistence yields often require some external inputs or irrigation. I suggest the authors provide a more thorough explanation for using “subsistence yields” as a proxy for “agricultural suitability.”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_1|13", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Line 377 - Section “Statistical Analysis”: I would like to see the set of “equations” used. This would be a good way of summarizing the information that is, in fact, quite dense. These “equations” could simply be the instructions used in R to define the statistical models, or some schematic illustrations of how variables and parameters are related.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_1|14", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "The authors say that “to deal with overdispersion, we reran the species richness models substituting the Poisson distribution with a negative binomial distribution and dropping the random effect for site.” (my emphasis) Maybe this wasn’t necessary given that the model is a mixed-effects model (a consequence that is more clearly understood under the Bayesian approach). In these models there is hierarchical structure where the mean of the Poisson is being modeled with some distribution. For example, when the mean of a Poisson distribution is modelled by a gamma distribution, then the resulting distribution is a negative binomial. In other words, when using a Poisson with a mixed-model/hierarchical model, the overdispersion is automatically being taken care of (e.g., the Wikipedia: https://en.wikipedia.org/wiki/Negative_binomial_distribution) or McElreath, R. (2020). Statistical rethinking: A Bayesian course with examples in R and Stan. Chapman and Hall/CRC). This may be somehow related to the authors’ observation in lines 637-638.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_1|16", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Line 692: Can you say that often “species with large global ranges” are generalists?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_1|18", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Lines 726-728: I don’t understand the conclusion: “This suggests that species richness and abundance increases with rice yield in landscapes with a high percentage of natural habitat is driven by narrow-ranged species.”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_1|20", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Line 785: There is a reference to straight lines (most likely correctly) and then a reference to Figures 4 and 5, but these do not depict straight lines. This is a little bit confusing because the relationship between the straight lines first mentioned and the results in the figures is not clear.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_1|21", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Figure 1a: Why do some “dots” have different color intensities (e.g., in South America)?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_1|22", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Figure 1b: The relative size of the circles is too similar. Why are some points circumferences and others circles?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_1|23", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Figure 1c: I don’t understand this plot. What is the meaning of the “axes”? What is the “grey square”?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_1|25", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "What is the meaning of the dashed red lines in figures S5-S12?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_1|26", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "ATTENTION: Some of the figures have the same “number” (two figures S5, two figures S9, and two S14).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "For comparison of intensification and expansion, both scenarios aim at reaching the same production increase target of +1%.\n\nThis seems arbitrary to me, and it is not explained why 1% is chosen. Further, the assumptions underlying the two land use scenarios are very normative and I am afraid that the assumptions also largely determine the results. The authors write that their chosen scenarios are not realistic projections for the future, but rather capturing an extreme case of possible strategies to increase agricultural production.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Nevertheless, there is no theory behind, what is driving agricultural expansion/intensification and where this is gonna happen. Changing these assumptions could probably lead to very different results and conclusions, which affects the robustness of the approach. As an example, expansion is only allowed into primary vegetation and takes place at each pixel up to the 1% production increase target in the comparison scenario. The 1% production increase target applies to every pixel. Why e.g. not implementing a global production increase target? Yields are increased uniformly on each pixel by 1%, unless a yield increase by 1% in regions with low yields (high yield gaps) increases absolute yields only very marginally.\n\nTherefore, closing yield gaps by a certain percentage value would have been more intuitive. It would also be more realistic to assume that yield increases are stronger in regions with high yield gap, due to the fact that yield gaps are already almost reached (and even above in some regions) in high productive regions.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "In case of expansion, more land is used and no land is taken out of production and restored to natural ecosystems, which is a major reason why land use expansion in average is worse for biodiversity, at least if you look at this at the landscape scale. Accordingly, linking your approach to the land sparing/land sharing debate is difficult, and therefore, in my opinion, your conclusion is biased in that regard. What you would have to do is to intensify in each pixel e.g. by 10%, then reducing the used land to reach the 1% production increase target and restore natural ecosystems on the freed up land. Would that be possible?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "[Data and Methods] It is not easy to follow the methodology at first reading due to the many different data sets. I had to read several sections twice. An overview is missing, which would help a lot to quickly understanding the used data and methods. Therefore, I suggest showing a schematic figure for both, the yield-biodiversity models and the land-conversion models, giving an overview on the applied data and how they were used.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "[Data and Methods] The time period the authors target their scenario is approximately the year 2000 and not a future projection, considering climate change, etc., which would make the study more interesting.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "[Data and Methods] Instead of using potential yield estimates by Mueller, that are based on observed yields within AEZs, you could use potential yields, simulated by crop models, which take spatial heterogeneity and future climate change impacts into account. They tend to be higher than observation based approaches, especially in developing countries.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "In the discussion, I would additionally expect one sentence saying that also other ecosystem services rather than biodiversity must be considered in an integrative approach, such as carbon storage and water infiltration, etc.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "I am wondering if you consider any kind of maximum expansion potential, which limits agricultural expansion mainly in bread basket regions, because available areas for expansion are very limited here.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_2|10", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "While the study gives interesting new surprising findings and a new view on the effects of land intensification on agriculture, I am still not fully convinced that these findings are robust and not a result of the assumptions and the conceptual framework of the approach. This needs to be clarified. Therefore, I suggest major revisions of the manuscript.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_2|11", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "I suggest to use the term “cropland” instead of “farmland” in the title, because farmland could include pasture areas or rangeland which is not considered in your approach.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_2|12", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "[Abstract] While you quantify the effect of intensification on biodiversity in the abstract by a median species loss of 11%, you just say that land conversion is associated with significant biodiversity loss”. I suggest to give quantitative results for both aspects for comparison, which would improve the significance and informative value of the abstract.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_2|13", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "[Figures] Figure titles are used instead of figure subtitles, which confused me. Maps are not well illustrated. I'd suggest to use a global frame and cut at -60° South (showing all global maps without Antarctica).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_2|14", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Ln 25: “yield increases also lead to” instead of “yield also lead to …”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_2|15", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Ln 42: Which has already been done by some other studies, e.g. Zabel et al. (2019). https://doi.org/10.1038/s41467-019-10775-z", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_2|16", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Ln 51: , whereas", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_2|17", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Ln 66-70: This is an important aspect, referring to the discussion on sustainable intensification, which could also be mentioned here as a buzzword. Nevertheless, sustainable intensification is not considered in your approach, which I assume, would impact on the comparison between expansion and intensification quite drastically, also to the authors’ conclusions. That should also be added to the discussion. Also, I would be interested in an explanation, what kind of intensification this data driven statistical approach implies in different regions and how this could impact on biodiversity?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_2|18", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Ln 211-213: At least for rice, I assume that rainfed systems are also not used by subsistence farmers, but honestly I don’t know.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_2|19", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Ln 364-367: This is an important limitation of this study, because usually cash crops might be used at much higher intensity level than other crops. Also, I guess that there is a huge difference between crops. I was wondering if ‘cropping system’ is the right term here? Maybe, ‘across different crops’ might be more accurate?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_2|20", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Ln 452: blank before full stop.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_2|21", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Ln 476-478: This is an important assumption for understanding the whole study and I have been missing this information while reading the chapters before. I was always wondering, where expansion and intensification takes place and by how much you close yield gaps, etc. Now this is explained here. You expand and close yield gaps to reach a uniform production increase by 1% for each pixel and each crop. Maybe mention that already earlier, maybe end of introduction where you describe the general study framework.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_2|22", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Line 484: If you increase the area by 1%, you assume homogeneous yields within a pixel, which may not be correct. I guess this overestimates yields, because usually, the best land is already in use and cropland is expanded into less productive land, at least in human modified landscapes. Another issue might be that expanded land often is used at lower intensity, while you assume the same yield gap than for the rest of the area within the pixel, which may not be the case. These assumptions should be addressed and/or discussed.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_2|23", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Ln 488: In the previous part of the article, including the abstract, you mention closing the yield gap. Also Figure 4 is showing the effects of closing yield gaps (not saying by how much, I assume fully closing). However, increasing yields uniformly by 1% is s.th. else than closing yield gaps by 1%. You do not explicitly say that you close yield gaps by 1%, but at least reading the previous parts, it gives the impression and therefore, the text is somehow confusing in this context.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_2|24", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Ln 488: Another question relating to these very small intensification levels in regions with large yield gaps is the question if the statistical approach is sensitive enough to capture the impacts on biodiversity of such small absolute yield changes? Especially for subsistence farmers, inter-annual yield variabilities are much higher than 1% meaning that a yield increase of 1% cannot significantly be related to changes in management.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_2|25", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Ln 592-602: Not clear at first reading: Does this refer to a land conversion of all primary vegetation or to the +1% production increase scenario?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_2|26", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Appendix Figure S23. Source missing.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "This global study examines the biodiversity effects of land conversion, and of two major strategies, namely increasing yield on the same land area, or expanding farmed area without intensification. These questions have been explored before. For instance, in a recent study by Jaureguiberry et al (2022, Science Adv), they found that land/sea conversion is the primary cause of biodiversity loss. The two major strategies, known as the \"land sharing / land sparing dilemma,\" have also been the subject of numerous articles, many of which have concluded that there is no easy answer because it depends on the context. Therefore, I have some doubts regarding the novelty of these results. Nevertheless, it utilized quantitative ecology data from a diverse array of taxa, indicators and locations, thus, being probably the most comprehensive study, utilizing several global database/estimates.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "This study is extensive, with Figure 3 alone providing a broad variety of results to analyse, like why are there many relationships (like for soy and RCAR), while none in others (wheat and RCAR). The article analysed biome, crop, biodiversity indicators, landscape context, land use, and their interactions. However, only a limited number of results were emphasized and described in the paper.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "I find it difficult to fully endorse the prioritization of yield over factors such as fertiliser consumption, particularly when the focus is solely on biodiversity benefits and socio-economic aspects are not taken into account in the study. Productive land can achieve high yields without relying heavily on agrochemicals, but low quality areas may experience low yields despite using large amounts of fertilizers. Consequently, in the second scenario, the yield is low, but the negative impact on biodiversity is greater.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Biotic homogenisation is a measure of community composition, restricted to spatial context. Note, however, that this not characterise the species in the community, as range sizes are influenced by human activities, e.g. via extirpation of suitable habitats.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Why 1% increase in total production was targeted? 5% or 10% increase would be also interesting. As we now that c 800 million people are starving and we are 8 billions, a 10% would be realistic. On the other hand, however, if food system would be effective (no waste, no overconsumption /c. 900 million live with obesity/, etc.), what biodiversity gain would be if 1%, 5% or 10% decrease in yield will be possible?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "I enjoyed the presentation of study limitations (from line 773), as it listed several of my concerns I noted while reading the manuscript, like missing of local scale, data/database quality, straight line across the maps. So this is a valuable part of the paper, clarifying its uncertainties. But these exist. In addition, the models not fully fit assumptions. Thus, results need some caution when interpreting.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_3|7", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "What is closing the yield gap? Define.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_3|8", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Line 42: From this point, the introduction is on land sharing/sparing. However, these terms are ignored from the abstract, making a little bit of mismatch between these sections.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_3|9", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Line 56-57. \"Neither species persistence or community metrics response to yield increases were assessed globally\" it is true but, Martin et al (2019, Ecol Letters) published a large study on yield and landscape at the European scale.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_3|10", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Line 97-98: why 30 and 70% are the shares?", "reviewer_type": "human", "label": "error", "error_type": "Neglect", "label_origin": "expert+llm-filter"}
{"id": "prb|41|Human_3|11", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Line 123: where are Table S1-2-3? Not elegant to start with Table S4.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_3|12", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Figure 1. Looking at the map, I have the impression that the distribution of sites is aggregated, that is similar sites are clustered spatially. E.g. natural localities in natural landscapes are in SE Asia and Oceania, while Europe is the opposite. Thus, a conclusion that biodiversity decline is due to human ecosystem modifications can also be a spatial effect, that is the “treatments” are in different biogeographic regions. How to separate geography and human influence variables?\n\nThere are also pale blue circles (in Chile and Argentina, Japan, NE America). Is this a typo, or has some meaning? 1/c figure. I cannot understand it....", "reviewer_type": "human", "label": "error", "error_type": "Neglect", "label_origin": "expert+llm-filter"}
{"id": "prb|41|Human_3|13", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Fig.2. Increase the distance between a) and b), otherwise there is overlap in Y axis legend.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_3|15", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Fig.3. It has an extreme amount of information, really need time to digest it. Interesting to see that two graphs are empty, while others have a lot relationships plotted.\n\nAlso interesting to see that abundance and RCAR show similar trends in maize and soy, indicating more individuals in more homogenised communities -> a potential threat of invasions parallel with yield increase?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_3|17", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "In figure 3 several relationships show only one curve, that with the most data points. It ease illustration and understanding on a complex figure, but are the other relationships presented somewhere? Did not the reader miss some important results?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_3|19", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Line 606: typo: space is missing.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_3|20", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Line 645: Yes, but the blue colour (increase of richness) is rather clearly dominates tropical areas, like S Amazonia, and SE Asia. So the truth that increase in yield in the tropical areas has both benefits and costs on richness, while mostly costs in the temperate zone.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_3|22", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "L763: Others concluded that multifunctional landscapes are needed, a combination of sharing and sparing lands (Grass et al 2021, Adv Ecol Res).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_3|23", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Supplementary tables: there was probably some converting problem, a few letters were misplaced by „?”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_3|24", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Explain what is SR as this acronym was not used before.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_3|25", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "RCAR 55km is also new name (it was RCAR before).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_3|26", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Table S7, first column, correct column width to have „abundance” in one line.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|41|Human_3|27", "source": "prb", "split": "test", "paper_id": "prb41", "comment": "Supplementary figs: Fig S23: what is the dimension of the scale? %?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Claude|1", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "The paper's central finding that fragmentation importance decreases by approximately 30% for species with high-quality matrices is derived by comparing variable importance rankings between two Random Forest models with vastly different predictive performances—a methodologically problematic approach that undermines the validity of this key conclusion.\n\n\"Our model showed good overall classification ability during cross-validation, with 82% of species correctly classified. The accuracy in predicting high-risk transitions (sensitivity = 61.7%) was lower than the accuracy in predicting low-risk transitions (specificity = 84.4%), with a true skill statistic of 0.5.\"\nThe main model achieves a TSS of 0.5, which is considered moderate performance. However, this is contrasted with the high-quality matrix model performance in the comparison that follows, where the disparity becomes problematic for drawing comparative conclusions about variable importance.\n\n* Quote (from Table 1): \"Extinction risk transitions ~ High-quality matrix: Accuracy 81.7, Sensitivity 34.8, Specificity 83.7, TSS 0.2\"\nThe high-quality matrix model has a TSS of only 0.2 with sensitivity of 34.8%, meaning it correctly identifies only about one-third of high-risk species. A TSS of 0.2 is generally considered poor model performance [[1]](#references). Comparing variable importance rankings from a model with such poor predictive ability to one with moderate performance (TSS 0.5) is methodologically problematic because the variable importance in a poorly performing model may not accurately reflect the true relationships between predictors and the outcome.\n\"We found that the degree of fragmentation had a higher relative predictive performance for species with low-quality matrix (Fig. 4a) than that observed for species with low-quality matrix (Fig. 4b), with a decrease of 30.1%.\"\nThis 30% decrease in fragmentation importance is the paper's key finding supporting the title claim that matrix condition mitigates fragmentation effects. However, this comparison is drawn between models with TSS of 0.5 (low-quality matrix model, derived from Table 1 context) and 0.2 (high-quality matrix model). When a model fails to correctly classify 65% of high-risk species, the relative variable importance rankings become unreliable because the model is essentially not capturing the drivers of high-risk transitions for most species.\n\"The relative importance of a variable importance measures is context-dependent and can be misleading when the model's overall performance is poor.\" [[2]](#references)\nLiterature on Random Forest variable importance emphasizes that importance measures should only be compared between models with similar performance. Comparing importance rankings from models with vastly different TSS values (0.5 vs 0.2) violates this principle, making the 30% decrease in fragmentation importance potentially an artifact of differential model performance rather than a real ecological relationship.\n\nReferences:\n[1] Allouche, O., Tsoar, A. & Kadmon, R. (2006). Assessing the accuracy of species distribution models: prevalence, kappa and the true skill statistic (TSS). *Journal of Applied Ecology*, 43, 1223–1232. https://doi.org/10.1111/j.1365-2664.2006.01214.x\n[2] Scikit-learn documentation. Permutation Importance vs Random Forest Feature Importance (MDI). https://scikit-learn.org/stable/auto_examples/inspection/plot_permutation_importance.html", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Claude|2", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "The methods section claims to use the \"Actual Impurity Reduction Importance metric\" citing Nembrini et al. (2018), but the provided code instead uses the permutation-based MeanDecreaseAccuracy from the randomForest R package—a different metric that is not the AIR importance described in the cited reference.\n\n\"We measured the predictive importance of each variable using the Actual Impurity Reduction Importance metric\\(^{92}\\). This metric is unbiased with regard to the number of categories in the variables, and it computes reliable importance estimates without the extra computing cost of permutations.\"\nThe paper explicitly states that the Actual Impurity Reduction (AIR) importance metric was used, which according to Nembrini et al. (2018) [[3]](#references) is implemented in the `ranger` R package, not in the `randomForest` package. The AIR is specifically designed to be an unbiased impurity-based importance measure that corrects for variable selection bias in standard Gini importance.\n\n* Quote (from code file `5. RF_high_medium_first_last.R`):\n\n```r\nimportance.values<-data.frame(highHFP.drivers.RF$importance)\nimportance.mean.decrease.accuracy<-data.frame(names=importance.values$names, importance=importance.values$MeanDecreaseAccuracy, class=importance.values$class)\n```\nThe code extracts `MeanDecreaseAccuracy` from the randomForest model output, which is the permutation-based importance measure (also known as Mean Decrease in Accuracy or MDA), not the Actual Impurity Reduction importance. This is fundamentally different from the AIR described in Nembrini et al. (2018), which is an impurity-based measure with bias correction. The code also uses the `randomForest` package rather than `ranger` where AIR is implemented.\n\n* Quote (from code file `5. RF_high_medium_first_last.R`):\n\n```r\nlibrary(randomForest)\nhighHFP.drivers.RF<-randomForest(trans_first_last~., data=trainset, ntree=ntreebm, mtry=mtrybm, importance=TRUE)\n```\nThe code uses the `randomForest` package, which provides two importance measures: MeanDecreaseAccuracy (permutation importance) and MeanDecreaseGini (impurity importance). Neither of these is the AIR importance described in Nembrini et al. (2018). The AIR importance is specifically available in the `ranger` package with the option `importance = \"impurity_corrected\"`. This discrepancy between stated methods and actual implementation affects reproducibility and the interpretation of results.\n\"In ranger, it is possible to compute two additional VIMs: the unscaled permutation importance and the actual impurity reduction (AIR), proposed by Nembrini, König, and Wright (2018).\" [[4]](#references)\nThe ranger package documentation confirms that AIR importance is specific to ranger and not available in randomForest. Since the code uses randomForest and extracts MeanDecreaseAccuracy, the paper's methods description does not match the actual implementation, which could affect the reproducibility and validity of results.\n\nReferences:\n[3] Nembrini, S., König, I. R. & Wright, M. N. (2018). The revival of the Gini importance? *Bioinformatics*, 34, 3711–3718. https://doi.org/10.1093/bioinformatics/bty373\n[4] Wright, M. N. & Ziegler, A. (2017). ranger: A Fast Implementation of Random Forests for High Dimensional Data in C++ and R. *Journal of Statistical Software*, 77(1), 1–17. https://doi.org/10.18637/jss.v077.i01", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Claude|3", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "The Random Forest model correctly predicts only 61.7% of high-risk species transitions (sensitivity), meaning nearly 40% of species that experienced increased extinction risk are misclassified, which raises concerns about the reliability of conclusions regarding what environmental factors drive high-risk transitions.\n\n\"Our model showed good overall classification ability during cross-validation, with 82% of species correctly classified.\"\nWhile 82% overall accuracy appears good, this metric is misleading given the class imbalance in the dataset. With 67.2% of species in the low-risk category and 32.8% in the high-risk category, a classifier that simply predicts all species as low-risk would achieve approximately 67% accuracy. The model's improvement over this baseline is modest, and the high overall accuracy is largely driven by correctly classifying the majority class.\n\"The accuracy in predicting high-risk transitions (sensitivity = 61.7%) was lower than the accuracy in predicting low-risk transitions (specificity = 84.4%), with a true skill statistic of 0.5.\"\nA sensitivity of 61.7% means the model misclassifies 38.3% of species that actually experienced increased extinction risk. For a study aimed at understanding what drives species toward higher extinction risk, failing to correctly identify more than one-third of high-risk cases represents a substantial limitation. The conclusions about which variables are most important for predicting high-risk transitions should be interpreted cautiously given this level of misclassification.\n\"For imbalanced classification, the sensitivity might be more interesting than the specificity. [...] A feature is 'important' if shuffling its values increases the model error.\" [[5]](#references)\nLiterature on imbalanced classification emphasizes that when the minority class (here, high-risk species) is of primary interest, sensitivity is the key metric to evaluate. The paper's claim of \"good overall classification ability\" downplays the substantial misclassification rate for the class of primary conservation interest. Variable importance measures are influenced by how well the model predicts both classes, and substantial errors in predicting high-risk transitions may affect the reliability of importance rankings for understanding what drives extinction risk increases.\n\"However, it is important to acknowledge that the exclusion of other variables associated with pressure (such as overhunting, disease, invasive species, and climate change) and life-history traits (such as rarity, dispersal mode, and ranging behavior) could have increased the uncertainty of our predictions, and thus influenced the ability of our models to correctly classify high-risk transitions.\"\nThe authors acknowledge this limitation, but the moderate sensitivity combined with known missing predictors suggests that the conclusions about the relative importance of fragmentation versus other factors may not fully capture the actual drivers of high-risk transitions. The paper's strong claims about fragmentation being more important than habitat loss and amount should be tempered by this acknowledged model limitation.\n\nReferences:\n[5] Brownlee, J. (2020). Tour of Evaluation Metrics for Imbalanced Classification. *Machine Learning Mastery*. https://machinelearningmastery.com/tour-of-evaluation-metrics-for-imbalanced-classification/", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Claude|4", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "The study uses habitat suitability models built for the year 2000 as a static representation of suitable habitat and matrix, while analyzing extinction risk changes over a 24-year period (1996-2020), introducing potential temporal mismatches that could affect the validity of the fragmentation-extinction risk relationship.\n\n\"We used habitat suitability models developed by Rondinini et al.49 to represent the extent of suitable habitat patches and the extent of the matrix of 4,327 out of 5,722 extant terrestrial mammals, corresponding to 76% of all species in the group75. These models were built for the year 2000 at a spatial resolution of 300 m.\"\nThe habitat suitability models are static snapshots from the year 2000. However, both habitat extent and configuration would have changed substantially over the 24-year study period (1996-2020), particularly for species in regions experiencing rapid land-use change. Using static habitat maps to calculate fragmentation metrics may not accurately represent the actual fragmentation experienced by species throughout the period when their extinction risk was changing.\n\"Spatially explicit data on the condition of the matrix...was obtained from the recently updated global human footprint maps51. These maps represent the most comprehensive global distribution of changing human pressure on the environment at 1 km resolution between 2000 and 2013.\"\nThe Human Footprint change is measured only for the period 2000-2013 (13 years), while extinction risk transitions span 1996-2020 (24 years). This temporal mismatch means that human pressure changes before 2000 and after 2013 are not captured, potentially underestimating the total human pressure change that corresponds to the observed extinction risk transitions.\n\"In identifying extrinsic variables, we favoured those datasets with a good temporal match with the period over which extinction risk transitions were observed.\" [[6]](#references)\nPrevious extinction risk modeling work by some of the same authors emphasized the importance of temporal matching between predictor variables and the period of observed extinction risk changes. The use of static 2000 habitat suitability models with a 1996-2020 extinction risk study period does not achieve this temporal alignment, potentially introducing noise into the fragmentation-extinction risk relationship.\n\"However, there is also the possibility that the loss of most suitable habitat patches had already occurred before the beginning of the study period, resulting in fragmentation being a more important predictor of extinction risk than habitat loss and habitat amount.\"\nThe authors acknowledge this possibility, which directly highlights the problem with temporal mismatch. If substantial habitat loss occurred before 2000 (the year of the habitat suitability models), the static models would not capture this loss, while the Human Footprint change variable (starting in 2000) would also miss it. This could artificially inflate the apparent importance of fragmentation relative to habitat loss if loss preceded the measurement period while fragmentation effects persisted.\n\nReferences:\n[6] Di Marco, M., Venter, O., Possingham, H. & Watson, J. (2018). Changes in human footprint drive changes in species extinction risk. *Nature Communications*, 9, 4621. https://doi.org/10.1038/s41467-018-07049-5", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Claude|5", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "The comparison between low-quality and high-quality matrix models is based on substantially different sample sizes (3,779 vs. 452 species), with the high-quality matrix group having only 12% of the species, which may contribute to the poor model performance and unreliable importance rankings for this subgroup.\n\n\"'low-quality matrix', representing species with \\( \\geq 50\\% \\) of the extent of their matrix overlapping with high human footprint values (\\( n = 2,529 \\) low-risk species and 1,250 high-risk species); and 'high-quality matrix', representing species with \\( < 50\\% \\) of the extent of their matrix overlapping with high human footprint values (\\( n = 341 \\) low-risk species and 111 high-risk species).\"\nThe low-quality matrix model is trained on 3,779 species (2,529 + 1,250), while the high-quality matrix model is trained on only 452 species (341 + 111). This represents a more than 8-fold difference in sample size. Additionally, the high-quality matrix group has only 111 high-risk species, which is a small sample for building a reliable classifier of extinction risk transitions, especially when using Random Forest with cross-validation.\n\n* Quote (from code file `6. RF_quality_matrix.R`):\n\n```r\nlow.quality.matrix<-highHFP.drivers %>% filter(high_hfp_extent_unsuitable>84.210526)\nhigh.quality.matrix<-highHFP.drivers %>% filter(high_hfp_extent_unsuitable<15.789474)\n```\nThe code shows the threshold used to define high-quality matrix (< 15.79% high HFP extent) captures only a small subset of species. The severe sample size reduction for the high-quality matrix group, combined with the imbalanced ratio of high-risk to low-risk species (111:341, approximately 1:3), likely contributes to the poor sensitivity (34.8%) observed in this model. Small sample sizes can lead to unstable variable importance estimates and unreliable model performance in Random Forest classification.\n\"Random Forest modelling has shown to have the highest performance among several machine learning techniques tested for the prediction of global extinction risk of terrestrial mammals.\"\nWhile Random Forests are generally robust, their performance depends on having sufficient training data, particularly for the minority class. With only 111 high-risk species in the high-quality matrix training set, and using 75% for training (approximately 83 species), the model has limited examples from which to learn the characteristics of high-risk transitions in high-quality matrix environments. This may explain the poor sensitivity (34.8%) and overall TSS (0.2) for this subgroup.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|GPT|1", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "This paper operationalizes “changes in extinction risk” using a binary label that largely reflects persistent threat status (species retaining categories) rather than genuine temporal change, undermining the validity of conclusions about drivers of *change* in extinction risk.\n\n\"Here, we quantify the relationship between changes in the extinction risk of 4,327 terrestrial mammals over a 24-year period (1996-2020), the degree of fragmentation of their suitable habitat, and the levels of human pressure within the associated habitat matrix.\"\nThis sentence frames the response as a temporal *change* in extinction risk over 1996–2020, which implies the labels should primarily track deterioration/improvement events. However, the paper’s later definition of the response groups includes large sets of species whose Red List category did not change, meaning the model is not isolating change processes. When most outcomes are stable, “change” language can be misleading because the model will be dominated by cross-sectional differences between persistently low- vs high-risk species. That in turn weakens claims about fragmentation or matrix condition driving *changes* over time, because the model is not primarily learning transitions. A common practice when focusing on trends is to use indicators explicitly designed to track genuine category changes over time (see evidence below), rather than mixing stable states with transitions.\n\"The low-risk group includes species that retain a category of least concern, together with those species that move from any higher category of threat to a lower category assessment period. The high-risk group includes all species that retain a category of threatened or near threatened, together with those species that move from any lower category of threat to a higher category over time.\"\nThese definitions explicitly include “retain” cases in both classes, so membership is not restricted to species whose status changed during the study period. As a result, the classifier conflates two different phenomena: (i) being threatened (or least concern) at the endpoints, and (ii) changing category over time. This matters because predictors of *current/persistent threat status* need not match predictors of *status transitions* (e.g., historical habitat loss vs recent fragmentation). The conflation can also distort interpretation of “transition” probabilities, since they include many species with no transition. A robust change-focused design would model genuine category changes as events (or model category trajectories) rather than bundling stable and changing species into the same binary outcome.\n\"When classifying extinction risk transitions with the initial and final Red List categories, we found that 4,029 (93.1%) species retained the same Red List category and 298 (6.9%) changed through time.\"\nThis supplementary result shows that true category changes are rare (6.9%), yet the main analysis labels 32.8% of species as “high-risk transitions,” which necessarily includes many non-transition cases. With such a low transition rate, any “transition” model is structurally dominated by endpoint status rather than temporal dynamics. That dominance makes it difficult to attribute findings to drivers of change, because the signal of real transitions is weak relative to the signal of stable categories. It also raises concerns about whether the study is answering the question it poses (drivers of change) versus a different question (correlates of low vs high risk). This is a major validity issue because it directly affects what the model is learning and what the reported variable importance can legitimately be said to explain.\n\"Most species that move between categories on The IUCN Red List (see the section Reasons for Changing Category) do so because of improved knowledge or revised taxonomy. It is therefore impossible to determine any meaningful trends in the status of biodiversity simply by looking at overall changes in numbers of threatened species between updates.\" ([\\[3\\]](#ref3))\nThis IUCN guidance highlights that naive use of category movements is not a reliable trend indicator because many changes reflect reassessment artifacts rather than genuine status change. While the paper attempts to incorporate retrospective assessments and genuine changes, its outcome definition still mixes stable categories with transitions and treats endpoint categories as “transitions,” which does not resolve the core interpretability problem. The quoted text also implies that if the goal is to infer trends, the analysis should isolate genuine changes and explicitly handle reasons for change. Without that, conclusions about “changes in extinction risk” risk being confounded by assessment processes rather than biological change. This is particularly important for global-scale comparative modeling, where heterogeneous assessment histories can systematically bias apparent transitions.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|GPT|3", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "This paper draws mechanistic and quasi-causal conclusions (e.g., “primarily determined” and “mitigated”) from Random Forest variable-importance rankings and interaction plots, which only establish predictive association and can be unreliable for inference about underlying drivers.\n\n\"This suggests that changes in species extinction risk are primarily determined by the fragmentation of habitat, and secondarily by the loss and the amount of habitat within species’ ranges.\"\nThe paper uses an importance ranking to make a strong determinative claim (“primarily determined”) about ecological drivers. However, Random Forest variable importance is a model-dependent summary of predictive contribution, not a causal effect size or a decomposition of explained variance that supports statements about primary vs secondary determinants. Such language risks overstating what the analysis can support, especially given observational confounding among habitat amount, fragmentation metrics, and human footprint. Even within a purely predictive framing, importance scores can shift with correlated predictors, preprocessing, and the chosen importance definition, making “primary” claims fragile. A more defensible approach would report the result as a predictive ranking under the specific model and explicitly avoid causal language unless supported by an identification strategy.\n\"Our results suggest that the negative effects of habitat fragmentation may be somewhat mitigated when the matrix is associated with lower levels of human pressure.\"\nThe word “mitigated” implies an intervention-like claim: improving matrix condition would reduce fragmentation’s effects on extinction risk. Yet the study design is observational and the modeling is primarily predictive, so the interaction pattern can reflect confounding (e.g., biogeographic covariation of matrix condition with other pressures) rather than a modifiable mitigation mechanism. Without explicit causal assumptions and checks (e.g., sensitivity analysis for unmeasured confounding, or quasi-experimental variation), such mitigation claims are not robust. This is especially important because the paper uses this framing to motivate restoration as a conservation action, which is a decision-relevant inference. Stronger practice in the field is to separate predictive association from actionable causal claims, or to validate mechanistic claims using independent data or natural experiments.\n\"We show that random forest variable importance measures are a sensible means for variable selection in many applications, but are not reliable in situations where potential predictor variables vary in their scale of measurement or their number of categories.\" ([\\[1\\]](#ref1))\nThis methodological result cautions against treating variable-importance outputs as stable evidence about underlying drivers when predictors differ in type or encoding, which is common in this paper (categorical diet/order/realm vs continuous fragmentation and footprint measures). Even if the authors aim for predictive ranking, the reliability of importance as an inferential signal depends on the importance definition and the data’s variable types. The paper’s conclusions about fragmentation’s dominance and matrix moderation depend directly on these importance comparisons, so any instability or bias threatens the robustness of the conclusions. This is not merely a software concern; it is a known methodological limitation of interpreting feature importance as scientific evidence about drivers. Addressing this typically requires robustness checks across importance definitions and explicit discussion of what importance can and cannot imply.\n\"In explanatory modeling f represents an underlying causal function, and X is assumed to cause Y. In predictive modeling f captures the association between X and Y.\" ([\\[2\\]](#ref2))\nThis distinction clarifies why predictive modeling outputs, including importance rankings and partial dependence summaries, do not by themselves justify causal language about determinants or mitigation. The paper’s core modeling approach is explicitly predictive (Random Forest classification with cross-validation), so the appropriate interpretation is associational. When a paper uses predictive tools to make mechanistic statements, standard practice is to either add a causal identification strategy or to rephrase conclusions to remain within predictive scope. Here, the manuscript’s language repeatedly implies causal influence of matrix condition on fragmentation’s effects, which goes beyond what predictive association can establish. This affects the reliability of the conservation recommendations because causal interpretability is central to claiming that restoration would mitigate risk.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|GPT|4", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "The study cannot be independently reproduced because key input layers are not openly available and core spatial processing requires proprietary ArcGIS/Spatial Analyst tooling, while the manuscript also states code is only available upon request.\n\n\"Habitat suitability models for the world’s terrestrial mammals are available upon request from the model developers (see https://globalmammal.org/habitat-suitability-models-for-terrestrial-mammals/).\" / \"All relevant codes used in this work are available upon request from the corresponding author (J.P.R.-D.).\"\nThese statements indicate that essential inputs (habitat suitability models) and the analysis code are not openly accessible to readers, preventing an independent reproduction of the pipeline. Because the spatial suitability models define “suitable habitat” and therefore directly affect fragmentation and matrix computations, withholding them blocks verification of the most important predictors in the paper. Similarly, “code available upon request” undermines reproducibility standards because access can be delayed, denied, or vary over time, and it prevents automated provenance checks. In computational ecology and conservation, a common expectation is that published claims can be verified using archived code and data snapshots, or at minimum a fully specified route to obtain them without ad hoc negotiation. This limitation materially affects whether reviewers and later researchers can validate the reported findings.\n\"Input data are available within each folder of this repository, except for the habitat suitability models, which were derived from another study and are available only upon request (see https://globalmammal.org/habitat-suitability-models-for-terrestrial-mammals/).\" / \"The scripts `4. High_HFP_extent_suitable_unsuitable.py` and `High_HFP_extent_medium_unsuitable_combined.py` require `ArcGIS Pro` version 2.8.2 or higher, and the `Spatial Analyst` license to run.\"\nThe repository README confirms that the primary spatial inputs are not included and adds a requirement for proprietary ESRI software and a paid extension license. This combination prevents fully reproducible, open execution in typical academic computing environments and complicates long-term archiving because licenses and versions change. For a global-scale study with multiple processing steps, reproducibility depends on being able to re-run spatial preprocessing end-to-end, not only downstream modeling scripts. If the key steps require non-open tooling, authors typically mitigate by providing derived intermediate outputs (e.g., per-species fragmentation/matrix metrics) and exact versioned workflows; the manuscript does not provide such a complete open alternative. As a result, readers cannot independently regenerate the core predictors used in the Random Forest models.\n```python\nimport arcpy\nfrom arcpy import env\nfrom arcpy.sa import *\n...\narcpy.CheckOutExtension(\"Spatial\")  \n```\nThis code snippet demonstrates that spatial preprocessing depends on ArcPy and the Spatial Analyst extension, which are not available in standard open Python environments. That dependence is not inherently invalid, but it raises a reproducibility barrier that should be compensated for by providing executable alternatives (e.g., open-source GIS implementations) or distributing fully processed predictor tables that can reproduce all figures. Given that the paper’s main claims rest on derived landscape metrics (fragmentation and matrix HFP overlap), inability to execute this step means the central variables cannot be independently verified. It also makes it hard to assess sensitivity to GIS implementation details (e.g., raster processing rules, projection handling, distance transforms). Therefore, the reliance on proprietary tooling contributes to a substantial reproducibility gap.\n\"All scholarly digital research objects2—from data to analytical pipelines—benefit from application of these principles, since all components of the research process must be available to ensure transparency, reproducibility, and reusability.\" ([\\[5\\]](#ref5))\nThis statement articulates widely adopted expectations for computational research objects: reproducibility depends on access to the full pipeline, not just a narrative description. In this paper, key pipeline components (habitat models and a proprietary GIS stack) are not available in a way that enables transparent re-execution by independent researchers. That directly conflicts with the goal of making the study’s claims checkable and reusable, especially for a high-impact conservation application. The issue is not simply “open science” preference; it affects error detection, sensitivity analyses, and the ability to extend the method to new taxa or time periods. Without accessible pipeline components, peer review cannot fully assess whether the reported fragmentation and matrix metrics were computed as described.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|GPT|5", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "The manuscript’s reporting of Wilcoxon tests is internally inconsistent (rank-sum vs signed-rank), and the provided R code uses incorrect argument names and settings, calling into question the correctness and reproducibility of the reported p-values and effect-size comparisons.\n\n\"When looking at the difference in the degree of fragmentation for low-risk and high-risk species, we found that those classified as high-risk had higher degrees of fragmentation, with a difference that was significant for each of the levels of quality of the matrix (\\( p \\)-values < 0.001; Wilcoxon signed rank test, one-sided).\"\nThis sentence reports a “Wilcoxon signed rank test,” which is the paired-sample Wilcoxon test, and it also specifies a one-sided direction. However, the comparison described (low-risk vs high-risk species) is between independent groups, not paired observations, so a signed-rank test would generally be inappropriate unless a pairing scheme is explicitly defined. Misnaming the test can mislead readers about the data structure, assumptions, and interpretation of the p-value. This matters because the significance claim is used to support the narrative that fragmentation differs systematically between risk groups under different matrix qualities. A correct and transparent statistical description should match the study design (independent vs paired) and the implemented test.\n\"We also used Wilcoxon rank sum tests to test for statistical differences in the degree of fragmentation between low-risk and high-risk species restricted to the defined levels of quality of the matrix.\"\nThis methods sentence instead specifies a Wilcoxon rank-sum test (Mann–Whitney), which is the standard choice for comparing two independent groups. The inconsistency between “rank sum” here and “signed rank” in the results makes it unclear what test was actually performed and therefore what p-values mean. Such ambiguity is significant because nonparametric tests can differ in null hypotheses and applicability depending on pairing. It also affects reproducibility: an independent reanalysis cannot know which test to run to match the paper. Resolving this would require consistent reporting of the exact test, sidedness, and whether any pairing or stratification was used.\n```r\n#Run Wilcoxon rank sum test\nwilcox.test(degree.habitat.fragmentation.low.quality.matrix~transition.low.quality.matrix, mu=0, alt=\"g\", conf.inf=T, conf.level=0.95, paired=F, exact=T, correct=T, data=degree.habitat.fragmentation.low.quality.matrix)\n```\nThis code indicates an unpaired (`paired=F`) two-sample test, aligning with a rank-sum design rather than a signed-rank design, contradicting the “signed rank” wording in results. More importantly for reproducibility, the function call uses argument names `alt` and `conf.inf`, which are not the standard argument names shown in R’s documentation (`alternative` and `conf.int`). In typical R execution, misspelled/unknown arguments can raise errors (“unused argument”) or lead to silently ignored settings depending on how the call is parsed, meaning the actual test run (including one-sidedness and confidence interval computation) may not match what the authors intended. The code therefore does not provide a reliable, executable reference implementation for the reported statistics. Given the emphasis on p-values < 0.001, uncertainty about the exact test specification is a major statistical-reporting flaw.\n\"wilcox.test(x, y = NULL, alternative = c(\\\"two.sided\\\", \\\"less\\\", \\\"greater\\\"), mu = 0, paired = FALSE, exact = NULL, correct = TRUE, conf.int = FALSE, conf.level = 0.95, ...)\" / \"If only x is given, or if both x and y are given and paired is TRUE, a Wilcoxon signed rank test ... is performed. Otherwise, if both x and y are given and paired is FALSE, a Wilcoxon rank sum test ... is carried out.\" ([\\[7\\]](#ref7))\nThis documentation provides the authoritative argument names and clarifies the difference between signed-rank (paired/one-sample) and rank-sum (unpaired two-sample) Wilcoxon tests in R. It shows that `alternative` and `conf.int` are the correct argument names, so the code’s `alt` and `conf.inf` are inconsistent with the documented interface. It also makes clear that signed-rank vs rank-sum is determined by whether the test is paired; the code uses `paired=F`, which corresponds to a rank-sum test, not a signed-rank test. Therefore, the manuscript’s results text (“signed rank test”) and the provided code cannot both be correct as written. This inconsistency undermines confidence in the reported inferential statistics supporting matrix-quality-stratified fragmentation differences.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "The paper claims to disentangle the effects of habitat fragmentation from habitat amount and concludes that fragmentation is a stronger predictor of extinction risk. However, the metric used for fragmentation (\"average Euclidean distance within patches of suitable habitat from the nearest patch edge\") is strongly correlated with the metric used for habitat amount (\"proportion of suitable habitat\"), with a Spearman correlation of 0.76 in the provided dataset. This high collinearity undermines the validity of the Random Forest variable importance comparison and the conclusion that fragmentation is more important than habitat amount.\n\n\"Central to the debate has been a persistent uncertainty in disentangling the effects of habitat loss on biodiversity from the effects of fragmentation per se, especially relative to the reduction in patch size and the increase in patch isolation\"\nThe authors explicitly state that disentangling these effects is a central goal of the study. However, using highly correlated metrics without controlling for habitat amount (e.g., by using residuals or selecting landscapes with independent variation) fails to achieve this goal.\n\"Importantly, we discover that fragmentation is a stronger predictor of risk than species life-history traits, habitat loss, and habitat amount.\"\nThis conclusion is based on the Random Forest variable importance ranking. When predictors are highly correlated (Spearman rho = 0.76), Random Forest variable importance measures can be unstable and biased, often splitting importance between correlated variables or arbitrarily favoring one. Therefore, the claim that fragmentation is \"stronger\" than habitat amount is not statistically robust given the confounding.\n\"For each species, we measured the degree of habitat fragmentation by quantifying the average Euclidean distance of all the pixels within patches of suitable habitat from the nearest patch edge\"\nThis metric is mathematically dependent on patch size and shape. As habitat amount decreases, patch sizes typically decrease, leading to a smaller average distance to edge. Thus, this metric is a proxy for habitat amount, as confirmed by the high correlation found in the data.\n\"Most measures of fragmentation are strongly correlated with habitat amount\" [1]\nFahrig (2003) highlights that many fragmentation metrics, including those related to patch size and edge distance, are intrinsically correlated with habitat amount, and that \"fragmentation per se\" effects can only be isolated by controlling for habitat amount. The authors fail to do this effectively. Furthermore, Ruffell et al. (2016) [2] and Didham et al. (2012) [3] emphasize the need for rigorous statistical approaches (e.g., structural equation modeling or residuals) to account for collinearity when disentangling these effects, which the current study lacks.\n\nReferences:\n[1] Fahrig, L. (2003). Effects of habitat fragmentation on biodiversity. Annual review of ecology, evolution, and systematics, 34(1), 487-515. https://www.annualreviews.org/doi/abs/10.1146/annurev.ecolsys.34.011802.132419\n[2] Ruffell, J., Banks-Leite, C., & Didham, R. K. (2016). Accounting for the causal basis of collinearity when measuring the effects of habitat loss versus habitat fragmentation. Oikos, 125(1), 117-125. https://onlinelibrary.wiley.com/doi/abs/10.1111/oik.02429\n[3] Didham, R. K., Kapos, V., & Ewers, R. M. (2012). Rethinking the conceptual foundations of habitat fragmentation research. Oikos, 121(2), 161-170. https://onlinelibrary.wiley.com/doi/abs/10.1111/j.1600-0706.2011.20270.x", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "The paper frames the analysis as predicting \"changes in species extinction risk\" and \"extinction risk transitions\". However, the data reveals that only 7.3% of the 4,327 species underwent a genuine change in IUCN Red List category between 1996 and 2020. The vast majority of species in the \"High-risk transition\" group are species that remained in a threatened category (Stable Threatened), and the majority in the \"Low-risk transition\" group remained Least Concern (Stable LC). Consequently, the model is primarily predicting static extinction risk status (threatened vs. non-threatened) rather than actual changes in risk, making the title and main conclusions about \"mitigating effects on risk change\" misleading.\n\n\"Here we measure the relationship between fragmentation, matrix condition (measured as the extent of high human footprint levels), and the change in extinction risk of 4,327 terrestrial mammals.\"\nThe authors frame the study around \"change in extinction risk\". However, an analysis of the provided data (`list_sp_with_genuine_changes.xlsx` and `historical_assessments.xlsx`) shows that only 315 species (7.3%) had genuine changes. The remaining ~93% had static status. This contrasts with the approach of focusing on genuine changes as recommended by Hoffmann et al. (2010) [5] for assessing trends in extinction risk.\n\"The low-risk group includes species that retain a category of least concern, together with those species that move from any higher category of threat to a lower category assessment period. The high-risk group includes all species that retain a category of threatened or near threatened, together with those species that move from any lower category of threat to a higher category over time.\"\nBy grouping \"retained\" status with \"changed\" status, the authors conflate static risk with changing risk. Since the \"retained\" species vastly outnumber the \"changed\" species, the model's predictive power is driven by the static correlates of extinction risk (which are well-known), rather than the correlates of *change* in risk.\n\"We find that the matrix condition and the fragmentation of habitat are strongly associated with changes in species extinction risk.\"\nThis conclusion is overstated. The association is likely with *being threatened* (static), not necessarily with *becoming threatened* (change). The distinction is crucial for conservation, as the drivers of current status (often historical) may differ from the drivers of recent decline.\n\nReferences:\n[5] Hoffmann, M., Hilton-Taylor, C., Angulo, A., Böhm, M., Brooks, T. M., Butchart, S. H., ... & Stuart, S. N. (2010). The impact of conservation on the status of the world's vertebrates. Science, 330(6010), 1503-1509. https://www.science.org/doi/abs/10.1126/science.1194442", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "The study defines \"matrix condition\" based on a single, low threshold of Human Footprint (HFP >= 3). While this threshold is justified by a previous study, it is relatively low (HFP ranges 0-50) and may classify semi-natural or low-intensity land uses (e.g., pasture) as \"unsuitable\" or \"high pressure\" matrix. Given that the central novelty of the paper is the effect of matrix condition, the lack of sensitivity analysis using alternative HFP thresholds (e.g., HFP >= 10, HFP >= 20) limits the robustness of the conclusions. It is unclear if the \"mitigating effect\" of matrix condition holds for different definitions of matrix quality.\n\n\"We define a human footprint threshold of >= 3 out of 50 to represent the extent of human-modified habitat within the matrix. This threshold was used as it has shown to be the strongest predictor of transitions in extinction risk for terrestrial mammals\"\nRelying solely on a threshold optimized in a previous study (Di Marco et al. 2018) [4] for a potentially different set of species or context is risky. HFP 3 is very low and might include areas that are permeable or suitable for many species.\n\"To test the sensitivity of our model, we built additional Random Forest models based on... a different combination of the levels of habitat suitability... and the extent of the matrix\"\nThe sensitivity analysis section mentions testing different *habitat suitability* definitions but notably omits testing different *matrix condition* (HFP) thresholds. This is a significant omission given the paper's title and focus.\n\nReferences:\n[4] Di Marco, M., Venter, O., Possingham, H. P., & Watson, J. E. (2018). Changes in human footprint drive changes in species extinction risk. Nature communications, 9(1), 4621. https://www.nature.com/articles/s41467-018-07049-5", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "As in any other article nowadays, it is of fundamental importance that the code developed, and all datasets associated with the study are provided in an online digital repository for anyone to use, and being able to replicate these results exactly. I was not able to confirm the results presented, unfortunately, and without that I can’t give a complete assessment of the study. Moreover, this needs to be open to the whole scientific community. Just stating that the code is available upon request is not enough. Please note that it must be ensured that the scripts provided are fully operational from any platform so I can run it on my machine if this manuscript comes back to me.", "reviewer_type": "human", "label": "error", "error_type": "Neglect", "label_origin": "expert+llm-filter"}
{"id": "prb|42|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "[Introduction] Line 92. Seems like there is an 'and' missing after environment? Otherwise the sentence doesn’t seem well constructed.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "[Introduction] Line 98. Why is chimpanzee behavioural activity relevant here? It only gets mentioned here and also in the methods, but doesn’t really add anything. It can be removed.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "[Results] Table 2. In the description of the variables, the average of the Euclidean distance (in the different metrics) must include an explanation of what is the average of. For example, in the fragmentation metric, is it the Euclidean distance from the centroid of each patch to the edge? If so, was the average taken across patches? Then, the ‘within’ is unclear.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "[Results] Lines 164-165. Not clear what you mean by: “This trend was reversed to an increased probability of low-risk transitions.”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "[Results] Figure 3. It is not clear how / why inverting the plot gives you the scenario for low-risk transition. This should be better explained. Also, I would suggest the authors to explore better ways of representing these data. The 3D plot is really challenging to understand / visualise correctly. This kind of plots are in general hard to understand if you can’t rotate them.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Human_1|9", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "[Results] Lines 178-179. How do the ‘sensitivity’ and ‘specificity’ values compare? It is not clear what does it mean when one is higher than the other and viceversa.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Human_1|10", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "[Results] Lines 199-200. ‘... predictive performance for species with low-quality matrix (Fig. 4a) than that observed for species with low-quality matrix...’ – One of those ‘low-quality matrix’ should be high-quality matrix.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Human_1|12", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "[Results] Lines 218-219. This sentence is not clear. Was the Wilcoxon comparison made between high and low risk, or between high and low quality, or combinatorially between both?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Human_1|13", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "[Results] Line 228. How can you know that this is an artifact of the ‘imbalance’ between low-risk and high-risk? There is no indication of why this should be the case. Also, please explain how was this ‘imbalance’ quantified.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Human_1|15", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "[Discussion] Line 256. It is the first time in the manuscript that the matrix quality has been linked to plant biomass. This should be a least mentioned, ideally well explained, much earlier.", "reviewer_type": "human", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|42|Human_1|16", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "[Discussion] Line 276. ‘helps confirms’ -> ‘confirms’", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Human_1|17", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "[Discussion] Lines 277-282. It would be nice to have a few lines here explaining how this work is an improvement on previous research. This paragraph gives the impression that most of it had been done before.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Human_1|18", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "[Discussion] Line 302. Suitable habitat was more important for what?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Human_1|20", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "[Method] Line 354. This is too vague. You need to explain fully how was the ‘expert information’ used and present it in an appendix and as part of the data made available.", "reviewer_type": "human", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|42|Human_1|21", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "[Method] Lines 355 – 358. Explain how the habitat suitability levels were decided and defined.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Human_1|22", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "[Method] Line 362. This is not clear. What do you mean by 'largest neighbour'? Aren’t all the pixels the same size?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Human_1|23", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "[Method] Line 382-383. Shouldn’t it be the other way around? i.e. large values of Euclidean distance representing LARGE rather than low degrees of isolation. Also, why not using the Euclidean distance between patches?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Human_1|24", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "[Method] Lines 410-413. This sentence is not clear. I couldn’t understand what you meant by this. Please rephrase.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Human_1|26", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "[Method] Line 456. ‘avoid potential circularity’ is vague. Please explain this. Why is there circularity and how is this a way of avoiding it.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "It is not completely clear how the range of a species is being defined. Does this use published distribution maps or is it based on the habitat suitability models? As matrix quality is assigned based on the human footprint of unsuitable habitat within the range of a species, how the range is defined is important. The amount and proximity of the matrix habitat to suitable habitat will be influenced by how the range maps are created. For example, if the maps are created to a high resolution with habitat suitability accounted for this will be very different to polygons constructed linking occurrence records. Please can this be clarified or made more prominent if already included.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "In the study the number of species with high-quality matrix and low-quality matrix were not equal but how were species with the two matrix types distributed with regard to geography and suitable habitat type (e.g. forest, grassland). If there are correlations between matrix quality and other bio-geographic variables how does this influence the interpretation of the results?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "Was structural contrast between the suitable habitat and matrix considered? More contrasting suitable and unsuitable habitat types are expected to result in stronger fragmentation effects. To a certain extent the quality of the matrix from the perspective of the focal species would therefore depend on how different it is from the suitable habitat. The majority of this is likely captured by the human footprint data used but there may be differences between biomes.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "Line 78 – what are the indications from smaller scale studies?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|42|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb42", "comment": "Line 361 – what size are the pixels?", "reviewer_type": "human", "label": "error", "error_type": "Neglect", "label_origin": "expert+llm-filter"}
{"id": "prb|43|Claude|1", "source": "prb", "split": "test", "paper_id": "prb43", "comment": "The paper claims that federated learning (FL) is effective for glioblastoma boundary detection but fails to provide a direct comparison between FL and centralized learning (CL) using equivalent data, making it impossible to attribute performance improvements to the FL methodology itself rather than simply having access to more data.\n\n\"At the time of initialization of the federation, the public initial model was evaluated against the local validation data of all sites, resulting in an average (across all cases of all sites) DSC per sub-compartment, of: DSC_ET = 0.63, DSC_TC = 0.62, DSC_WT = 0.75.\"\nThe public initial model was trained on only 231 cases from 16 sites, while the FL consensus model was trained on 6,314 cases from 71 sites. This represents approximately a 27-fold difference in training data. Comparing these two models and attributing improvements to FL is fundamentally flawed because the improvement could be entirely due to increased data volume rather than the FL approach itself. A proper experimental design would require training a CL model on the same pooled data for direct comparison.\n\"Notably, the only difference between the public initial model and the final consensus model, was that the latter gained knowledge during training from increased datasets contributed by the complete set of collaborators.\"\nThe authors explicitly acknowledge that the key difference is access to increased datasets, yet they frame this as demonstrating FL effectiveness. This experimental design confounds the effect of data quantity with the effect of the FL methodology. Without a CL baseline trained on the same 6,314 cases, one cannot conclude whether FL specifically contributed to improvements or whether any training method with access to the same data would achieve similar or better results.\n\"Co-authors in this study have previously introduced FL in healthcare in a simulated setting and evaluated different FL approaches for the same use case as the present study [...] Findings from these studies supported the superiority of the FL approach used in the present study (i.e., based on an aggregation server), which had almost identical performance to CL.\"\nThe paper references prior simulated studies showing FL performs similarly to CL but does not validate this finding in the current large-scale real-world study. Relying on prior simulated results while not providing equivalent validation in the present study is a methodological limitation, especially given that the current study operates at a much larger scale with significantly more heterogeneous data.\n\"Sheller et al. demonstrated that federated learning among 10 collaborating institutions would lead to model performance almost perfectly equivalent to that of centralized multi-institutional datasets.\" [[1]](#citation-list)\nOther studies in the field, such as the 2020 Sheller et al. study, explicitly compared FL against CL performance using the same underlying data. The current paper, despite claiming to be the largest FL study, does not include such a comparison, making its conclusions about FL effectiveness less rigorous than prior smaller-scale studies.\n\nReferences:\n[1] Sheller, M.J., Edwards, B., Reina, G.A., et al. \"Federated learning in medicine: facilitating multi-institutional collaborations without sharing patient data.\" Scientific Reports 10, 12598 (2020). https://doi.org/10.1038/s41598-020-69250-1", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|43|Claude|2", "source": "prb", "split": "test", "paper_id": "prb43", "comment": "The paper promotes FL as a privacy-preserving alternative to centralized learning but does not provide quantitative privacy guarantees, implement differential privacy, or evaluate vulnerability to known FL attacks such as gradient leakage and membership inference attacks.\n\n\"FL provides an alternative to train accurate and generalizable ML models, by only sharing numerical model updates.\"\nThe paper presents FL as inherently privacy-preserving by virtue of not sharing raw data. However, extensive research has demonstrated that sharing model updates (gradients or weights) can leak sensitive information about training data through gradient inversion attacks and membership inference attacks. The seminal work by Zhu et al. [[5]](#citation-list) showed that \"untrustworthy servers can even reconstruct user data\" from shared gradients. Simply not sharing raw data is insufficient for strong privacy guarantees.\n\"Additionally, we performed all operations on the aggregator on secure hardware (by leveraging trusted execution environments), in order to increase the trust by all parties in the confidentiality of the model updates being computed and shared, as well as to increase the confidence in the integrity of the computations being performed.\"\nWhile trusted execution environments (TEEs) protect computations on the aggregator, they do not address the fundamental privacy vulnerabilities in FL protocols. TEEs protect against certain threat models (e.g., malicious server operators) but do not prevent inference attacks from model updates shared by clients. The paper does not quantify privacy budgets or implement mechanisms like differential privacy that provide formal privacy guarantees.\n\"FL has been applied to multi-institutional neuroimaging and neuroscience studies, enabling cross-site learning on distributed MRI and brain imaging data while respecting strict data-sharing and human-subject constraints. [...] The assumption that FL alone is sufficient for robust privacy protection is challenged both theoretically and empirically. Theoretically, studies have demonstrated that decentralisation does not prevent attacks such as membership inference or gradient inversion.\" [[2]](#citation-list)\nContemporary literature on privacy-preserving FL explicitly recognizes that FL without additional safeguards remains vulnerable to privacy attacks. The reviewed paper does not address these well-documented vulnerabilities, implement differential privacy, or evaluate the model's susceptibility to such attacks, which is particularly concerning given the sensitive nature of medical imaging data.\n\"DP-SGD mechanism provides resilience against several known adversarial risks, including: Membership inference attacks, Gradient inversion and reconstruction, Statistical leakage and re-identification, Feature-level pattern extraction across heterogeneous subgroups.\" [[3]](#citation-list)\nState-of-the-art privacy-preserving FL implementations commonly incorporate differential privacy mechanisms (such as DP-SGD) to provide formal privacy guarantees. The absence of any such mechanism in this large-scale medical imaging study represents a significant gap in methodology given current best practices in the field.\n\nReferences:\n[2] \"A Systematic Review of Federated and Cloud Computing for Mental Health Prediction\" - PMC article discussing privacy vulnerabilities in federated learning. https://pmc.ncbi.nlm.nih.gov/articles/PMC12788194/\n[3] \"Privacy-preserving federated credit risk models\" - Nature Scientific Reports reference discussing differential privacy for federated learning. https://www.nature.com/articles/s41598-025-34536-9\n[5] Zhu, L., Liu, Z. & Han, S. \"Deep leakage from gradients.\" Advances in Neural Information Processing Systems 32 (NeurIPS 2019). https://proceedings.neurips.cc/paper/2019/hash/60a6c4002cc7b29142def8871531281a-Abstract.html", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|43|Claude|3", "source": "prb", "split": "test", "paper_id": "prb43", "comment": "The model selection process used local validation data from participating sites (which were part of the federated training infrastructure) to select the final consensus model, potentially introducing bias toward the participating sites' data distributions and limiting the reliability of out-of-sample performance estimates.\n\n\"After the training process was complete, the 'final consensus model' was obtained after model selection from all the global consensus models obtained for each federated round.\"\nModel selection was performed using consensus models from different rounds, but the selection criterion (local validation data) comes from the same sites that participated in training. This creates a potential information leak where the model selection process is informed by data that, while not directly used in training, comes from the same institutional distributions that trained the model.\n\"To quantitatively evaluate the performance of the trained models, 20% of the total cases contributed by each participating site were excluded from the model training process and were used as 'local validation data'.\"\nWhile the 20% local validation split prevents direct data overlap, these validation cases still come from the same 49 training sites. If the training process causes models to overfit to characteristics specific to these institutions (scanner types, preprocessing artifacts, patient demographics), the local validation data would not detect this overfitting because it shares these characteristics. True generalizability can only be assessed on data from completely different sites.\n\"To further evaluate the potential generalizability improvements of the final consensus model on unseen data, we compared it with the public initial model against the complete out-of-sample data, and noted significant performance improvements of 15% (p_ET < 1×10^−5), 27% (p_TC < 1×10^−16), and 16% (p_WT < 1×10^−7).\"\nWhile out-of-sample evaluation on 6 held-out sites is valuable, this evaluation was performed after the final model was selected using local validation data. A more rigorous approach would involve selecting the model based on a separate validation set that is independent of all participating sites, or using cross-validation across sites during the federated training process. The reported out-of-sample improvements, while significant, could be inflated if the model selection process inadvertently favored models that also performed well on similar (but not identical) data distributions.", "reviewer_type": "ai", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|43|GPT|1", "source": "prb", "split": "test", "paper_id": "prb43", "comment": "The manuscript’s statistical claims about performance gains and model-optimization trade-offs are not interpretable or reproducible because the statistical tests are not specified, and the manuscript uses p-values in a way that conflates (or obscures) statistical and practical significance.\n\nFollowing model training across all sites, the final consensus model garnered significant performance improvements against the collaborators’ local validation data of 27% (\\(p_{ET} < 1 \\times 10^{-36}\\)), 33% (\\(p_{TC} < 1 \\times 10^{-59}\\)), and 16% (\\(p_{WT} < 1 \\times 10^{-21}\\)), for ET, TC, and WT, respectively (Fig. 1.c).\nThis sentence reports extremely small p-values but omits the statistical test (e.g., paired Wilcoxon vs. paired t-test), the unit of analysis (per-patient, per-slice, per-site), and whether the test accounts for within-site clustering and repeated measures. In multi-institution medical imaging, these design choices materially affect validity because correlations (multiple scans per patient, patients nested within sites) can make naïve tests anticonservative. Without an explicit test and sampling unit, a reader cannot reproduce the p-values nor assess whether they correspond to clinically meaningful improvements versus an artifact of a large effective sample size. The omission also prevents assessing multiplicity, since p-values are reported for multiple tumor regions and multiple evaluation sets. This weakens the manuscript’s inferential claims beyond descriptive reporting.\nTo further facilitate use in low-resource environments, we plan to publicly release run-time optimized\\(^{81}\\) version of the final consensus model. ... These optimizations yielded several run-time performance benefits, such as lower inference latency ... while the trade-off was an insignificant (\\(P_{Average} < 7 \\times 10^{-5}\\)) drop in the average \\(DSC\\).\nThe manuscript labels a change as “insignificant” while simultaneously reporting a very small p-value threshold, which is internally ambiguous unless the authors explicitly distinguish “statistical insignificance” from “practical insignificance.” If the intent is to argue practical insignificance, the manuscript should report effect sizes (absolute DSC change), uncertainty intervals, and a pre-specified equivalence/non-inferiority margin rather than a p-value. If the intent is statistical insignificance, the reported p-value contradicts that interpretation. This matters because the quantization step is presented as safe for clinical deployment decisions, and readers need a clear, statistically coherent claim. As written, the statistical rationale does not support the conclusion.\nA p-value, or statistical significance, does not measure the size of an effect or the importance of a result. [[5]](https://www.amstat.org/asa/files/pdfs/p-valuestatement.pdf)\nThis American Statistical Association guidance directly contradicts using a p-value threshold to justify that a DSC change is “insignificant” in any practical sense, unless an explicit effect-size framework is provided. In a large dataset (thousands of cases), even tiny effect sizes can yield extremely small p-values, so a p-value alone cannot justify a claim of negligible clinical impact. The manuscript’s reporting aligns with a common misuse the ASA warns against: treating p-values as a proxy for importance. A more appropriate approach would report the DSC delta, confidence intervals, and (if needed) equivalence testing around a clinically justified margin. Because this paper emphasizes clinical deployment in “low-resource environments,” conflating these concepts is a substantive validity issue. The ASA statement thus provides a field-standard benchmark that the manuscript does not meet.\n\nReferences:\n[5] [American Statistical Association, “Statement on Statistical Significance and P-Values” (2016)](https://www.amstat.org/asa/files/pdfs/p-valuestatement.pdf)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|43|GPT|2", "source": "prb", "split": "test", "paper_id": "prb43", "comment": "The manuscript does not specify the aggregation rule used to combine client updates (e.g., whether averaging is weighted by local sample counts), which is a core methodological detail in federated learning and can materially bias training outcomes under heterogeneous site sizes.\n\nThe central aggregation server received model updates from all collaborators, combined them (by averaging model parameters) and sent the consensus model back to each collaborator to continue their local training.\nThis description is ambiguous about whether the averaging is weighted by each site’s number of training examples/cases, which is the standard approach in FedAvg-style optimization for heterogeneous client data volumes. In multi-site medical imaging consortia, site sizes can vary by orders of magnitude, so unweighted averaging implicitly upweights small sites and can change both convergence and final performance. Because the paper’s key claim is that scaling to 71 institutions improves generalizability, the aggregation rule is central to attributing gains to “more data” versus “different weighting.” Moreover, the paper later attributes improvements to increased datasets, making the omission especially problematic for causal interpretation. Without this detail, independent reproduction (even with the provided codebase) cannot verify that the described training matches FedAvg or another algorithm.\nTo quantitatively evaluate the performance of the trained models, 20% of the total cases contributed by each participating site were excluded from the model training process and were used as “local validation data”.\nThis sentence makes clear that each site contributes its own number of cases, implying that the federation combines updates coming from sites with potentially different dataset sizes. In such settings, the aggregation rule (case-weighted vs. site-weighted averaging) defines what objective the federation optimizes and can substantially affect both convergence and the final model. The manuscript does not report the distribution of cases across sites nor whether aggregation is weighted by site sample counts, leaving a key piece of the FL methodology unspecified. Because the paper’s central narrative is that “big data” and global diversity drive generalizability, the reader needs to know whether the optimization actually emphasizes larger contributors or treats all sites equally. Without that detail, it is difficult to interpret whether performance gains reflect scaling data volume, changing the effective weighting across institutions, or both. This ambiguity is therefore a substantive methodological gap affecting the validity of the reported training protocol.\nand the server then takes a weighted average of the resulting models. [[1]](https://arxiv.org/abs/1602.05629)\nThis FedAvg reference makes explicit that aggregation is typically weighted by client data size (\\(n_k\\), \\(|D_u|\\), or equivalent), precisely to reflect the global objective over all examples rather than over clients. The manuscript under review uses language (“averaging model parameters”) that could describe either weighted or unweighted averaging, but does not clarify which was implemented. Given that the paper’s central claim is “big data” via multi-site federation, aligning aggregation with sample counts is not a minor implementation detail; it defines what “big data” means in the optimization objective. If the authors did something different, they must justify it and quantify sensitivity to that choice, especially under heterogeneous site contributions. The lack of this clarity prevents readers from comparing the approach to standard FL baselines and from evaluating whether improvements are attributable to data scale or algorithmic weighting.\n\nReferences:\n[1] [McMahan et al., “Communication-Efficient Learning of Deep Networks from Decentralized Data” (arXiv:1602.05629)](https://arxiv.org/abs/1602.05629)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|43|GPT|4", "source": "prb", "split": "test", "paper_id": "prb43", "comment": "The manuscript’s main empirical claims emphasize percentage improvements (e.g., 33% improvement) without reporting the absolute post-training DSC values (and their uncertainty), making it difficult to assess robustness, clinical significance, and whether gains are consistent across sites and tumor subregions.\n\nWe demonstrate a 33% improvement over a publicly trained model to delineate the surgically targetable tumor, and 23% improvement over the tumor’s entire extent.\nThis statement is a central headline result, but it does not define whether “improvement” is absolute DSC difference, relative percent change in DSC, or another metric transformation. Because DSC is bounded in [0,1], relative improvements can appear large even when the absolute change is modest (or vice versa), and the clinical impact depends on absolute segmentation quality and error modes. The statement also does not specify on which evaluation set(s) these improvements are computed (local validation vs. out-of-sample vs. aggregated out-of-sample), which affects the generalizability claim. In multi-institution settings, aggregate improvements can also mask regressions at particular sites or cohorts; without per-site breakdowns and uncertainty, the conclusion is fragile. As written, the result is not sufficiently anchored to a reproducible quantitative definition.\nAt the time of initialization of the federation, the public initial model was evaluated against the local validation data of all sites, resulting in an average (across all cases of all sites) \\(DSC\\) per sub-compartment, of: \\(DSC_{ET} = 0.63\\), \\(DSC_{TC} = 0.62\\), \\(DSC_{WT} = 0.75\\). ... we then calculate the average \\(DSC\\) ... as equal to 0.66.\nThe manuscript reports baseline absolute DSC values but does not report the corresponding absolute DSC values for the final consensus model, instead switching to relative improvements. This prevents readers from assessing whether the final model reaches performance levels consistent with clinical utility expectations for segmentation tasks and whether improvements differ by sub-compartment. It also makes it hard to compare against external benchmarks (e.g., BraTS leaderboards or prior publications) that typically report absolute DSC distributions. Because the paper emphasizes “paradigm shift” and potential deployment, absolute performance is not optional context; it is necessary to evaluate conclusions. The absence of final absolute DSC (with dispersion measures) therefore materially weakens the interpretability and credibility of the reported gains.\nFollowing model training across all sites, the final consensus model garnered significant performance improvements ... of 27% ... 33% ... and 16% ...\nReporting improvements as percentages without giving the final values (or even baseline and final paired summaries per region) makes it impossible to assess whether the improvements are driven by a subset of cases (e.g., low baseline performance cases) or are uniform. In medical segmentation, it is standard to report at least median and interquartile range (or mean±SD) across cases, often stratified by subregion, because distributions are typically skewed and include failure cases. The figure caption suggests violin/box plots exist, but the main text still omits the numerical final values needed for secondary analyses and comparisons. Without uncertainty intervals, the clinical relevance of the gains cannot be judged, especially given the paper’s emphasis on rare disease and underrepresented populations. This undermines the robustness of the conclusions.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|43|GPT|5", "source": "prb", "split": "test", "paper_id": "prb43", "comment": "Although the manuscript links to multiple code repositories, it does not provide versioned, runnable artifacts that uniquely identify the exact pipeline and trained model(s) used for the reported results (and it states that model release is planned), which limits independent reproducibility and third-party validation.\n\nMotivated by findability, accessibility, interoperability, and reusability (FAIR) criteria in scientific research\\(^{84}\\), all the code used to design the Federated Tumor Segmentation (FeTS) platform for this study is available at https://github.com/FETS-AI/Front-End.\nThis statement provides a general link but does not pin the exact version (commit hash/tag) or a minimal set of commands/configuration files that recreate the reported 71-site training run (e.g., site selection, split logic, stopping criteria, aggregation rule, model selection rule, preprocessing parameters). In federated learning, reproducibility depends not only on model architecture and learning rate, but also on orchestration details (round scheduling, client weighting, failure handling) and data preprocessing harmonization. Without versioned artifacts, independent researchers cannot verify that their execution matches the paper’s described procedure, even if they have access to similar data. The manuscript also does not identify a checksum or release identifier for the “public initial model” weights, which is a critical starting point for the reported convergence and improvements. Thus, the code availability claim does not, by itself, ensure reproducibility of the reported findings.\nTo further facilitate use in low-resource environments, we plan to publicly release run-time optimized\\(^{81}\\) version of the final consensus model.\nThe wording indicates that the key trained artifact (the final consensus model, especially the optimized deployment version) is not yet available as part of the submission, despite being central to the paper’s claimed clinical impact. For independent validation, model weights (and inference scripts) are often the most practical artifact when raw clinical data cannot be shared, enabling evaluation on external datasets and auditing of failure cases. A “planned” release cannot support the current conclusions at review time, especially given the manuscript’s framing around deployment and paradigm shift. Without access to the model, readers cannot test robustness to distribution shift, scanner variation, or annotation differences on their own cohorts. This materially affects the paper’s reproducibility and the strength of its claims.\nAccess to working code and models is required to make this type of research actionable for others. [[4]](https://pmc.ncbi.nlm.nih.gov/articles/PMC8082347/)\nThis reproducibility guidance (in the context of medical imaging AI) articulates a community expectation that goes beyond citing repositories: the artifacts must be complete and usable to allow replication, reuse, and auditing. The manuscript under review provides multiple links but does not provide a clearly scoped, complete, and versioned “release” corresponding to the reported experiments (including trained weights), so it falls short of making the results readily actionable. This is especially important because the core dataset is not publicly available; in that case, models and full configurations become the primary route to independent evaluation. Without them, the work risks being difficult to build upon or validate, regardless of its scale. The issue therefore affects both reproducibility and the reliability of the conclusions.\n\nReferences:\n[4] [Kitamura et al., “Reproducible Artificial Intelligence Research Requires Open Communication of Complete Source Code” (Radiology: Artificial Intelligence, 2020; PMC)](https://pmc.ncbi.nlm.nih.gov/articles/PMC8082347/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|43|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb43", "comment": "The paper utilizes the standard Federated Averaging (FedAvg) algorithm without comparing it to or justifying the exclusion of more advanced algorithms designed to handle non-IID data, such as FedProx or SCAFFOLD.\n\n\"The central aggregation server received model updates from all collaborators, combined them (by averaging model parameters) and sent the consensus model back to each collaborator to continue their local training.\"\nThis description confirms the use of the standard Federated Averaging (FedAvg) algorithm. While FedAvg is a standard baseline, it is known to suffer from \"client drift\" and slow convergence when data is non-IID (independent and identically distributed), which is inherent in multi-site medical imaging studies.\n\"varying characteristics of the mpMRI data due to scanner hardware and acquisition protocol differences\\(^{52,53}\\) were handled at each collaborating site via established harmonized preprocessing pipelines\\(^{54-57}\\).\"\nThe authors acknowledge the heterogeneity of the data. However, preprocessing alone does not eliminate statistical heterogeneity (e.g., label distribution skew). Advanced FL algorithms like FedProx are specifically designed to address this issue by adding a proximal term to the local objective, often leading to better performance and stability in such settings.\n\"Federated optimization in heterogeneous networks\" [1]\nThis paper introduces FedProx and demonstrates that it significantly outperforms FedAvg in heterogeneous networks. The failure to compare with such methods leaves it unclear whether the reported performance is optimal or if significant gains were missed.\n\"Communication-Efficient Learning of Deep Networks from Decentralized Data\" [3]\nEven the original FedAvg paper acknowledges the challenges of non-IID data. Subsequent literature has established that for highly heterogeneous data, standard averaging is often suboptimal.\n\nReferences:\n[1] Li, T., Sahu, A. K., Zaheer, M., Sanjabi, M., Talwalkar, A., & Smith, V. (2020). Federated optimization in heterogeneous networks. Proceedings of Machine Learning and Systems, 2, 429-450. https://arxiv.org/abs/1812.06127\n[3] McMahan, B., Moore, E., Ramage, D., Hampson, S., & Arcas, B. A. Y. (2017). Communication-efficient learning of deep networks from decentralized data. Artificial intelligence and statistics, 1273-1282. https://arxiv.org/abs/1602.05629", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|43|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb43", "comment": "The paper relies on Trusted Execution Environments (TEEs) to protect the aggregation process but fails to address the risk of gradient leakage (inversion) attacks, which can reconstruct private training data directly from the model updates.\n\n\"we performed all operations on the aggregator on secure hardware (by leveraging trusted execution environments\\(^{77}\\)), in order to increase the trust by all parties in the confidentiality of the model updates being computed and shared\"\nThe authors assume that protecting the aggregation computation via TEEs is sufficient for privacy. However, TEEs only protect the code execution at the server; they do not prevent the *output* of the aggregation (the global model) or the *inputs* (if intercepted before the TEE) from leaking information.\n\"Deep Leakage from Gradients\" [2]\nThis paper demonstrates that it is possible to reconstruct training data (e.g., images) with pixel-level accuracy solely from the gradients shared in federated learning. This \"gradient inversion\" attack works even if the aggregator is honest-but-curious or if the communication channel is compromised.\n\"Secure, privacy-preserving and federated machine learning in medical imaging\" [4]\nThis review highlights that while FL offers privacy benefits, it is not immune to attacks. It emphasizes the need for additional privacy-preserving techniques like Differential Privacy (DP) or Homomorphic Encryption to prevent reconstruction attacks, which the current paper does not discuss or implement.\n\nReferences:\n[2] Zhu, L., Liu, Z., & Han, S. (2019). Deep leakage from gradients. Advances in Neural Information Processing Systems, 32. https://arxiv.org/abs/1906.08935\n[4] Kaissis, G. A., Makowski, M. R., Rückert, D., & Braren, R. F. (2020). Secure, privacy-preserving and federated machine learning in medical imaging. Nature Machine Intelligence, 2(6), 305-311. https://www.nature.com/articles/s42256-020-0186-1", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|43|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb43", "comment": "The paper acknowledges data heterogeneity but fails to quantitatively analyze the degree of non-IIDness (statistical heterogeneity) across the participating sites, which is a critical factor influencing FL performance.\n\n\"varying characteristics of the mpMRI data due to scanner hardware and acquisition protocol differences\\(^{52,53}\\) were handled at each collaborating site via established harmonized preprocessing pipelines\\(^{54-57}\\).\"\nThe authors rely on preprocessing to handle heterogeneity. However, they do not provide any metrics (e.g., t-SNE visualization of features from different sites, Kullback-Leibler divergence of label distributions) to quantify the residual heterogeneity.\n\"The data from all 55 collaborating sites followed a male:female ratio of 1.47 : 1 with age ranging between 7 and 94 years.\"\nListing demographic ranges is insufficient. In FL, \"label distribution skew\" (e.g., one site having mostly large tumors, another mostly small) is a major challenge. Without quantifying this, it is difficult to assess the difficulty of the task and the robustness of the reported results.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|43|Gemini|5", "source": "prb", "split": "test", "paper_id": "prb43", "comment": "The paper focuses solely on segmentation accuracy (DSC) and explicitly removes uncertainty estimation (ensembling) for efficiency, without evaluating the impact on model reliability or calibration, which is critical for clinical safety.\n\n\"we decided to proceed with a single 3D-ResUNet, rather than an ensemble of multiple models. This decision ensured a reduced computational burden, when compared with running multiple models, which is typically done in academic research projects\"\nThe authors explicitly trade off reliability (uncertainty estimation via ensembles) for computational efficiency. In a clinical setting, knowing *when* the model is uncertain is crucial for safety.\n\"Model performance was quantitatively evaluated here using the Dice Similarity Coefficient (\\( DSC \\))\"\nRelying only on DSC is insufficient for clinical deployment. Metrics like Expected Calibration Error (ECE) should be reported to ensure that the model's confidence scores align with its actual accuracy.\n\"On calibration of modern neural networks\" [6]\nThis paper highlights that modern neural networks are often poorly calibrated. For a system intended to \"drive patient care\", evaluating and ensuring calibration is a necessary step that this paper overlooks.\n\nReferences:\n[6] Guo, C., Pleiss, G., Sun, Y., & Weinberger, K. Q. (2017). On calibration of modern neural networks. International conference on machine learning, 1321-1330. https://arxiv.org/abs/1706.04599", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|43|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb43", "comment": "The methods, from a machine learning and federated learning standpoint, are all straightforward. Only one strategy for federated learning is utilized (a single, trusted server which serves as aggregator) the decision to utilize this strategy is unjustified in the work. Although there are clear situations where a single aggregator model makes perfect sense, and is in fact the optimal choice, many other federated learning strategies exist in the literature, and are useful in other situations. Single aggregator settings may not be desirable, for example, in settings where the trusted aggregator is distantly connected to some members of the consortium - multiple aggregators at different locations may be the better choice in this situation, especially if runtime is of concern. To be clear, I do not think that the authors made the incorrect choice by using the single aggregator paradigm; however, this is one example how the framework may not generalize outside of the choices the authors made for their own work.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|43|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb43", "comment": "Another significant gap is the lack of focus on data privacy in this work. To their credit, the authors do mention that federated learning both can provide solutions to privacy problems (don’t have to transfer data between sites) and can suffer from them (difficult to debug if private data causes problems) - these are both correct and important insights. Beyond this however, the only mention of security measures taken for the study is that collaborators “securely connected” to a central aggregation server, and that the aggregation server is “trusted”. In order to support these claims, more details are needed to establish what kinds of measures were taken.\\n\\nEven if more details were provided, a secure connection and trusted aggregators do not ensure data privacy, especially when model parameters are passed without perturbation between collaborators. Some fully-trained deep-learning models, for example, can be used to identify the participation of individuals in the data set (see for particular examples [1, 2] and [3,4] for nice surveys).\\n\\nI firmly believe that these issues of privacy are vitally important to consider in federated learning, and many efforts in the research community have been made in the community to address them (e.g. applications of differential privacy [4], many ). I do think it is a detriment to this work that no more details on privacy-preserving efforts are given, and I do think inclusion of some more detail on that front is necessary. I also believe that this further demonstrates that this work does not serve as a blueprint (privacy issues are especially nuanced!), and would like to reiterate my request that the authors tone down that claim. A sufficient blueprint would also need to do more work to address issues in federated learning such as stability to collaborator dropout, bottlenecks in communication between sites, financial considerations, and much more which this work does not.\\n\\n[1] Lam, Maximilian, et al. \\\"Gradient disaggregation: Breaking privacy in federated learning by reconstructing the user participant matrix.\\\" International Conference on Machine Learning. PMLR, 2021\\n\\n[2] Oh, Hyunseok, and Youngki Lee. \\\"Exploring image reconstruction attack in deep learning computation offloading.\\\" The 3rd International Workshop on Deep Learning for Mobile Systems and Applications. 2019.\\n\\n[3] Hu, Hongsheng, et al. \\\"Membership inference attacks on machine learning: A survey.\\\" ACM Computing Surveys (CSUR) (2021).\\n\\n[4] Liu, Ximeng, et al. \\\"Privacy and security issues in deep learning: A survey.\\\" IEEE Access 9 (2020): 4566-4593.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|43|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb43", "comment": "To move away from critical discussion - I do think the scope of the experiments and the work done are strong, and the study stands on its own as a particularly interesting application. The scope and diversity of the study is impressive, and the potential benefits to the research community are clear. I think, though, that this work would benefit more from taking pride in being a wonderfully fascinating case-study, and a marvelous exercise in large-scale federated learning, rather than a generic blueprint which future studies ought to follow - such a claim is simply beyond the scope of this otherwise strong work. In future work, I would encourage the authors to dig more into why certain choices are made during the federated methodology, and to justify why those decisions were made clear. I would also like to see more detailed discussion on how the administrative tasks were handled - I do firmly believe these insights would significantly benefit the community as a whole by providing a dimension of collaboration which is often omitted from technical papers.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|43|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb43", "comment": "Why was glioblastoma chosen? The rarity is not as rare as other such diseases so not sue if the FML will be as applicable as to say something like an endolymphatic sac tumor, or even low grade glioma for that matter.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|43|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb43", "comment": "How was the publicly trained model developed? Why not compare to established ML models?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|43|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb43", "comment": "What about distinguishing and identifying non enhancing glioblastoma?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|43|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb43", "comment": "Where did the FML have the most difficulty?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|43|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb43", "comment": "DSC is known to deliver higher numbers than IoU (Jaccard index). For a more rigorous evaluation, it would have been much more valuable to report both numbers.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|43|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb43", "comment": "The six sites selected for the out-of-sample generalization test (which is the main motivation for using FL) have been selected due to availability. This is rather a point of concern. Random selection would have been more reliable.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|43|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb43", "comment": "The data quality issue regarding erroneous reference annotations, or inherent variability, has not been properly addressed, among others, for the validation through six sites. Were the 590 cases delineated by one expert only?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|43|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb43", "comment": "A more in-depth and conclusive analysis regarding the comparison of the ensemble approach and the FL network is missing. Would a network of few major hospitals have the same effect as a complicated global network?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|43|Human_3|7", "source": "prb", "split": "test", "paper_id": "prb43", "comment": "Why were you not able to evaluate the exclusion of problematic sites like 48?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|43|Human_3|8", "source": "prb", "split": "test", "paper_id": "prb43", "comment": "Recent literature has not been mentioned. For instance:1) ProxyFL: Decentralized Federated Learning through Proxy Model Sharing\\n\\n2) Federated Learning with Differential Privacy: Algorithms and Performance Analysis\\n\\n3) Federated learning and differential privacy for medical image analysis\\n\\n4) Federated Learning for Computational Pathology on Gigapixel Whole Slide Images", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|44|Claude|1", "source": "prb", "split": "test", "paper_id": "prb44", "comment": "The paper claims to demonstrate end-to-end reproducibility of the Hosny et al. study, but the validation is limited to only one of the seven independent datasets used in the original work. The original multi-cohort study validated across 7 datasets from 5 institutions (1,194 NSCLC patients), while this replication only uses a subset of the NSCLC-Radiomics dataset (N=206 subjects). This significantly narrows the evidence supporting the claim that cloud infrastructure enables reproducible AI pipelines.\n\n\"Besides its impact on the field, another reason we chose this study for our use case was the fact that the AI pipeline was validated using an independent cohort now hosted by the IDC, i.e., the NSCLC-Radiomics dataset, allowing us to use the platform to reproduce the AI pipeline validation.\"\nThe authors explicitly acknowledge selecting the original study based on data availability rather than comprehensively reproducing the full validation scope. The NSCLC-Radiomics dataset was just one of seven external validation cohorts in the Hosny et al. study. True reproducibility would require validating across multiple cohorts to ensure the pipeline generalizes, yet this paper only demonstrates data fetching and processing on a single cohort. This limitation is significant because the original study's key contribution was demonstrating multi-cohort validation—an aspect not reproduced here.\n\"we compared our cloud-based pipeline with the original results shared by Hosny et Al. on a subset of the NSCLC-Radiomics dataset\"\nThe term \"subset\" further indicates that the validation is not even on the complete NSCLC-Radiomics cohort but a portion thereof. This raises concerns about selection bias and whether the demonstrated reproducibility would hold across the full dataset or additional cohorts. Multi-cohort validation is a cornerstone of establishing robustness in medical AI, as emphasized in guidelines such as CLAIM (Checklist for Artificial Intelligence in Medical Imaging) [[1]](#citation-1), which stresses the importance of external validation datasets for establishing generalizability.\n\"In the original work, the authors performed an integrative analysis on seven independent datasets across five institutions totaling 1,194 NSCLC patients\" from the project README\nThe README explicitly acknowledges that the original work validated across seven datasets, yet the cloud-based reproduction focuses only on one. This discrepancy between the original study's comprehensive validation and the limited scope of this reproduction significantly weakens the paper's claim to have demonstrated \"end-to-end replication.\" Reproducing only 14% (1/7) of the validation scope cannot be considered comprehensive reproducibility evidence.\n\nReferences:\n[1] Mongan, J., Moy, L. & Kahn, C. E., Jr. Checklist for Artificial Intelligence in Medical Imaging (CLAIM): A Guide for Authors and Reviewers. Radiol Artif Intell 2, e200029 (2020). https://pubs.rsna.org/doi/abs/10.1148/ryai.2020200029", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|44|Claude|2", "source": "prb", "split": "test", "paper_id": "prb44", "comment": "While the paper claims successful replication with \"no statistically significant difference,\" the Kaplan-Meier survival analysis shows a substantial degradation in statistical significance from p<0.001 in the original study to p=0.023 in the replicated pipeline. This order-of-magnitude difference in p-values indicates meaningful differences in patient stratification capability that merit deeper investigation rather than being dismissed as equivalent.\n\n\"We found that both the original pipeline and the replicated pipeline can successfully stratify higher-risk patients from lower-risk patients (p<0.001 and p=0.023, for the original and the replicated pipeline, respectively)\"\nWhile both p-values are below the conventional 0.05 threshold, the difference between p<0.001 and p=0.023 represents more than an order of magnitude change in statistical evidence. The original p<0.001 indicates extremely strong evidence against the null hypothesis, while p=0.023 represents only moderate evidence. In survival analysis, this degradation could have clinical implications when stratifying patients for treatment decisions. The paper does not adequately address why this discrepancy exists or what it implies for reproducibility.\n\n* Quote from README: \"After testing with various statistical tools, we observed that the difference between the results produced by the pipeline originally published by Hosny et Al. and those generated in our replication are not statistically significant (`p>0.05` for the two-sided Mann-Whitney U test and the DeLong test for paired AUC curves).\"\nThe authors focus on AUC comparison tests but do not provide similar formal statistical testing for the Kaplan-Meier stratification power difference. The lack of a formal test comparing the difference in log-rank test statistics between original and replicated pipelines represents an incomplete statistical analysis. As emphasized in literature on reproducibility [[2]](#citation-2), degradation in predictive performance during replication attempts deserves careful characterization rather than dismissal.\n\"As these masks are a newer iteration of the set of labels used for the original publication, we anticipated differences in the results.\"\nThe authors acknowledge using different segmentation masks, which could explain the statistical degradation. However, this admission undermines the reproducibility claim—if different inputs (updated masks) produce different outputs (degraded significance), then the pipeline is demonstrably sensitive to preprocessing variations. This contradicts the later claim that \"These results also prove the model's robustness to variation in the input segmentation mask.\" A 20-fold increase in p-value (from <0.001 to 0.023) does not support claims of robustness.\n\nReferences:\n[2] Yu, A. C., Mohajer, B. & Eng, J. External Validation of Deep Learning Algorithms for Radiologic Diagnosis: A Systematic Review. Radiol Artif Intell 4, e210064 (2022). https://pubs.rsna.org/doi/abs/10.1148/radiol.2018171820", "reviewer_type": "ai", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|44|Claude|4", "source": "prb", "split": "test", "paper_id": "prb44", "comment": "The paper makes broad claims about cloud infrastructure improving reproducibility in medical imaging AI but supports these claims with only a single case study (replication of one pipeline from one publication). This limited empirical evidence is insufficient to establish generalizability of the proposed approach across different AI pipelines, architectures, and application domains.\n\n\"Our approach demonstrates the potential of cloud resources for implementing, sharing, and using reproducible and transparent AI pipelines in medical imaging, which can accelerate the translation into clinical solutions.\"\nThis conclusion asserts broad applicability to \"AI pipelines in medical imaging\" based on a single reproduction attempt of one CNN-based prognostication model. Different AI architectures (transformers, diffusion models, ensemble methods) and application domains (segmentation, detection, classification) may present different reproducibility challenges that the proposed framework has not demonstrated it can address. Guidelines for AI reproducibility [[5]](#citation-5) emphasize that systematic evaluation across multiple studies is needed to establish reproducibility frameworks.\n\"We demonstrated that the proposed cloud-based infrastructure supports the replication of published AI literature.\"\nThe use of \"supports the replication of published AI literature\" (singular instance demonstrated, but broad claim made) represents an overgeneralization. The paper demonstrates one successful replication attempt with acknowledged limitations (different masks, statistical degradation). This does not constitute sufficient evidence to claim the infrastructure \"supports replication\" as a general capability. McDermott et al. [[6]](#citation-6) found that reproducibility in machine learning for health remains a significant challenge, with most studies failing to share adequate resources—a single success case does not address these systematic issues.\n\"Finally, the resources we provide can be easily extended to run the same analysis on any other collection hosted on the Imaging Data Commons, provided the dataset contains imaging data suited to the AI pipeline.\"\nThe qualifier \"provided the dataset contains imaging data suited to the AI pipeline\" acknowledges that the approach has limited applicability. Different AI pipelines have different data requirements, preprocessing needs, and computational demands. The paper does not demonstrate that its framework can accommodate this diversity, yet makes claims about its broad utility for \"transparent and reproducible AI-based medical imaging pipelines\" in general.\n\nReferences:\n[5] Varoquaux, G. & Cheplygina, V. Machine learning for medical imaging: methodological failures and recommendations for the future. NPJ Digit Med 5, 48 (2022). https://www.nature.com/articles/s41746-022-00592-y\n[6] McDermott, M. B. A. et al. Reproducibility in machine learning for health research: Still a ways to go. Sci. Transl. Med. 13, eabb1655 (2021). https://www.science.org/doi/10.1126/scitranslmed.abb1655", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|44|GPT|1", "source": "prb", "split": "test", "paper_id": "prb44", "comment": "The paper’s statistical support for “no statistically significant AUC difference” is undermined because the provided analysis notebook computes the DeLong test p-value incorrectly, which directly affects the claimed evidence in the Hosny et al. replication comparison.\n\n“After testing with various statistical tools, we observed that the difference between the results produced by the pipeline originally published by Hosny et Al. and those generated by our pipeline are not statistically significant (two-sided Mann-Whitney U test p>0.05, N=206; DeLong test for correlated (paired) AUC curves p>0.05, N=206).”\nThis sentence relies on the DeLong test p-value as a key piece of statistical evidence. If the implementation used to compute that p-value is wrong, then the evidentiary basis for the “not statistically significant” assertion is weakened, even if the qualitative conclusion might sometimes remain unchanged. Because this claim is central to their replication argument (and is presented as a quantitative justification), correctness of the p-value computation matters for validity. A reproducibility paper should be especially careful that the released code matches the described statistical procedure. Here, the notebook’s p-value conversion step is inconsistent with the output convention of the imported DeLong implementation. This is a major issue because readers who rerun or extend the notebook will propagate an incorrect statistical result.\n```python\n# Computes log(p-value) for hypothesis that two ROC AUCs are different\ndelong_log_pval = delong_roc_test(y_true, y_pred_baseline, y_pred_replication)\ndelong_pval = exp(delong_log_pval)\n\nprint(delong_pval)\n```\nThis code (from `hosny_results_comparison.ipynb`) converts `delong_log_pval` using `exp`, which assumes the value is a natural logarithm. However, the DeLong utility imported in this repository (see next evidence) returns a base-10 logarithm of the p-value, not a natural log, so `exp` is the wrong inverse transform. This makes the reported p-values numerically incorrect and therefore makes the quoted “p>0.05” evidence unreliable without independent correction. Even when both transforms yield values above 0.05 on this dataset, the magnitude of the p-value is still wrong, and in other settings this error could flip a decision around the threshold. Because the paper emphasizes transparent, inspectable statistical pipelines, this specific mismatch is a significant flaw. It also indicates the results were not cross-validated against a known-good DeLong implementation.\n```python\ndef calc_pvalue(aucs, sigma):\n    \"\"\"\n    Computes log(10) of p-values.\n    \n    Args:\n       aucs: 1D array of AUCs\n       sigma: AUC DeLong covariances\n    \n    Returns:\n       log10(pvalue)\n    \"\"\"\n    l = np.array([[1, -1]])\n    z = np.abs(np.diff(aucs)) / np.sqrt(np.dot(np.dot(l, sigma), l.T))\n    return np.log10(2) + scipy.stats.norm.logsf(z, loc=0, scale=1) / np.log(10)\n```\nThis code (from `src/utils/compare_auc_delong_xu.py`) explicitly documents that it “Computes log(10) of p-values” and returns `log10(pvalue)`. That means the correct conversion back to a p-value is `10**log10(pvalue)`, not `exp(log10(pvalue))`. Because the paper’s notebook uses this exact module (`from utils.compare_auc_delong_xu import delong_roc_test`) and then applies `exp`, the repository’s statistical pipeline is internally inconsistent. This is not a cosmetic bug: it changes the quantitative output that the manuscript cites as evidence. In a reproducibility-focused contribution, such an error directly contradicts the goal of providing reliably re-executable analyses. It also complicates independent verification because rerunning the shared notebook will not reproduce the intended statistical calculation.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|44|GPT|2", "source": "prb", "split": "test", "paper_id": "prb44", "comment": "The paper draws an unsupported conclusion that the replication discrepancy is “negligible” and that results “prove” robustness to segmentation-mask variation, even though the replication uses a different (newer) segmentation mask set and the reported non-significant p-values do not establish equivalence or robustness.\n\n“As these masks are a newer iteration of the set of labels used for the original publication, we anticipated differences in the results.”\nThis sentence is an explicit admission that the replication’s inputs differ from the original study in a way that can affect downstream predictions. Once a key input (segmentation) is changed, a small observed AUC change on a single cohort does not, by itself, demonstrate robustness of the model to segmentation variation in general. Robustness claims typically require systematic perturbation studies, multiple segmentation variants (or multiple annotators), and reporting of effect sizes/uncertainty across conditions. The paper does not present such a design here; instead, it reports one comparison on one cohort. Acknowledging the input difference is good transparency, but it simultaneously raises the bar for what can be concluded about robustness. Therefore, the later “prove robustness” statement is not supported by the described setup.\n“Therefore, we can conclude that the discrepancy between the two predictive models is negligible. These results also prove the model's robustness to variation in the input segmentation mask, as the original work claims.”\nThis is a strong inferential leap from a non-significant test result and a modest AUC difference (0.70 vs 0.68) to “negligible” discrepancy and “prove” robustness. Non-significance (p>0.05) does not imply equivalence, and it does not quantify how large a discrepancy could still be compatible with the data. To justify “negligible,” the paper would need an explicit equivalence margin (clinically or methodologically motivated) and confidence intervals on the AUC difference (or a formal equivalence test). To justify “robustness to segmentation,” it would need evidence across multiple segmentation perturbations, not just one newer label version. The manuscript also provides no analysis demonstrating that the segmentation change is the dominant driver of the AUC change, versus other pipeline differences. As written, the conclusion overstates what the evidence can support.\n“By convention a P value greater than 5% (P>0.05) is called “not significant.” … This term wrongly implies that the study has shown that there is no difference, whereas usually all that has been shown is an absence of evidence of a difference. These are quite different statements.” [[1]](#cite1)\nThis BMJ guidance directly contradicts the manuscript’s use of p>0.05 as justification for calling the discrepancy “negligible” and implying robustness. The quote explains that “not significant” commonly gets misread as “no difference,” which is precisely the logical step the paper takes when it states the discrepancy is negligible after observing p>0.05. In a replication context, the correct interpretation of non-significance is even more important because the goal is often to quantify similarity and identify failure modes, not merely to fail to reject a null. The BMJ note also emphasizes uncertainty and power issues, which matter here because an AUC difference of 0.02 could still matter depending on clinical context and sample size. Therefore, the paper’s conclusion is not statistically warranted under established statistical interpretation norms. The criticism is about the validity of the inference, not about whether the observed AUC values are “close.”\n“Likewise, a relatively large p-value does not imply evidence in favor of the null hypothesis; many other hypotheses may be equally or more consistent with the observed data.” [[2]](#cite2)\nThe ASA statement formalizes the point that a large p-value should not be treated as support for “no difference.” The paper uses p>0.05 to argue that the discrepancy is negligible and to “prove” robustness, which implicitly treats a large p-value as confirming the null (no meaningful difference). This is an interpretive error under the ASA’s consensus principles. Moreover, the ASA statement highlights that scientific conclusions should not hinge solely on thresholded p-values, whereas the manuscript’s key robustness conclusion is largely driven by threshold statements (p>0.05). The appropriate remedy would be to report uncertainty (e.g., confidence intervals for AUC difference) and define what difference would be practically important. Without that, the robustness claim remains ungrounded. This affects the reliability of the paper’s conclusions.\n```python\nmwustat, pval = stats.mannwhitneyu(y_pred_baseline, y_pred_replication)\n\nprint(mwustat)\nprint(pval)\n```\nThis code (from `hosny_results_comparison.ipynb`) applies a Mann–Whitney U test to the two sets of model scores. However, these scores are produced for the same set of patients (paired predictions), and Mann–Whitney U is an unpaired test that does not use within-subject pairing information. More importantly, even if correctly paired, a distributional test on raw scores is not an equivalence test for predictive performance and does not establish that the AUC difference is practically negligible. The notebook text frames this as a “starting point” for comparing outputs, but the manuscript elevates the resulting p>0.05 into a substantive “negligible discrepancy” conclusion. This strengthens the concern that the paper conflates “failure to detect a difference” with “no meaningful difference.” The statistical evidence as implemented is not sufficient for the strength of the claims made.\n\nReferences:\n[1] [Altman DG, Bland JM. “Statistics notes: Absence of evidence is not evidence of absence.” *The BMJ* (1995).](https://www.bmj.com/content/311/7003/485)\n[2] [Wasserstein RL, Lazar NA. “ASA Statement on Statistical Significance and P-Values.” *The American Statistician* (2016) (PDF).](https://www.burtthompson.net/uploads/9/6/8/4/9684389/wasserstein-2016__asa_p-value_statement.pdf)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|44|GPT|3", "source": "prb", "split": "test", "paper_id": "prb44", "comment": "The paper’s methodological claim that cloud notebooks make each pipeline step “examined and reproduced” end-to-end is not fully met by the released materials because key steps (model conversion) are explicitly not executable in the claimed environment, dependencies and runtime images are not pinned to immutable versions, and the main comparison notebook loads precomputed result CSVs.\n\n“By leveraging the National Cancer Institute’s (CRDC) Imaging Data Commons (IDC) component for data and the Google Cloud Platform (GCP) component for code and computing, each step within the AI pipeline - from data fetching and pre-processing, deep learning inference, data post-processing, and the analysis of the final results - can be examined and reproduced.”\nThis sentence commits to “each step” being reproducible, which sets a high bar for the artifact’s executability and environment capture. However, the repository documentation later admits that some essential steps (model conversion) cannot be run in Colab, and the project’s dependency specifications do not fully pin versions. In practice, end-to-end reproducibility requires that a reader can re-run all steps in a controlled environment, not only inspect code. The evidence below shows that at least one critical step depends on running a different Python version/stack outside Colab, which breaks the “examined and reproduced” promise in the main claimed environment. The claim also implies stability over time, but the provided Docker instructions and Python requirements do not ensure immutability. Therefore, the paper’s methodological conclusion overstates what the shared materials guarantee.\n“To convert the model from an older version of TensorFlow and Keras we need access to those libraries in the first place. As Google Colab does not support these older versions of such packages, these steps cannot unfortunately be run in a Google Colab notebook.”\nThis statement (from `code/src/model/README.md`) directly contradicts the manuscript’s broader framing that Colab notebooks eliminate the need for users to set up their own runtime environment for reproducibility. If a critical step (converting the model) cannot be executed in Colab, then reproducing the pipeline from raw model artifacts requires an external environment, which is a nontrivial barrier and a potential source of divergence. For a reproducibility-focused paper, such “out-of-band” steps should be minimized, fully containerized, and pinned to immutable versions. Otherwise, future readers may be unable to regenerate the ONNX model and must trust a provided artifact. This weakens the “end-to-end” nature of the claimed reproducibility. It also makes the pipeline less auditable, since conversion correctness is difficult to validate without rerunning it.\n```text\ndocker pull us-docker.pkg.dev/colab-images/public/runtime\n```\nThis instruction (from `code/README.md`) tells users to pull a Docker image without specifying a tag or digest. In container ecosystems, tags can be mutable and can point to different underlying images over time, meaning two users running the “same” command at different times may get different environments. This undermines the paper’s claim of a consistent and reproducible compute environment. It also shifts reproducibility risk onto external infrastructure changes, which the paper itself notes can happen, but does not mitigate in the released artifacts. For a paper advocating cloud-based reproducibility, recommending an unpinned runtime is a substantial methodological weakness. A stronger practice would be to pin the image by digest and/or publish an immutable container reference.\n“If no tag is specified, the image defaults to the `latest` tag.” [[4]](#cite4)\nThis Docker documentation explains why an unqualified `docker pull` can be unstable: it effectively selects `latest` and therefore a moving target. That directly supports the critique that the paper’s Docker-based “local Colab runtime” guidance does not provide an immutable environment snapshot. Because reproducibility requires controlling software versions, relying on a mutable default tag invites silent environment drift (OS packages, CUDA stack, Python base). This is particularly consequential for ML inference pipelines, where small dependency differences can alter numeric outputs or break execution. The paper positions the cloud as a route to standardized environments, but the provided instruction contradicts established container versioning practices. Therefore, the methodology as released does not fully support the end-to-end reproducibility claim.\n“Sigstore recommends referring to the image by digest and not by tag to avoid attesting to the wrong image, and attesting by tag will be removed in a future version of Cosign.” [[5]](#cite5)\nWhile this quote is about supply-chain attestation, it captures a broader best practice: tags are not stable identifiers, and digests are. The paper’s guidance to pull an unpinned Colab runtime image relies on tags (implicitly `latest`) rather than immutable digests, which is incompatible with strong reproducibility guarantees. In computational research artifacts, immutability is necessary not only for security but also for scientific reproducibility, because rerunning workflows must recreate the same environment. This quote supports the methodological argument that the paper should provide digest-pinned container references if it claims a standardized compute environment. Without such pinning, results can be non-reproducible despite “using the cloud.” Thus, the artifact design falls short of the paper’s reproducibility narrative.\n```text\nSimpleITK\npydicom\nmatplotlib\nseaborn\npandas\nnumpy\nonnx\nonnxruntime_gpu\npyplastimatch\nscikit-learn\nthedicomsort\n```\nThis dependency list (from `code/requirements.txt`) does not pin versions, even though the manuscript claims that tools “are packaged and versioned and can thus be recovered and installed at any point in time.” Unpinned dependencies are a well-known source of non-reproducibility because future installs may resolve to different major versions with changed APIs or numerical behavior. This is especially relevant for packages like `onnxruntime_gpu`, `SimpleITK`, and `scikit-learn`, where version changes can affect inference compatibility and evaluation outputs. A reproducibility-focused release would typically include exact versions and, ideally, a lockfile or container image digest that freezes the environment. The absence of version pins means that even if the notebooks run today, they may fail or change behavior later. This materially weakens the transparency/reproducibility claims.\n```python\n# analysis baseline: Hosny et al. results\nreplicated_csv_name = 'nsclc-radiomics_reproducibility.csv'\nreplicated_csv_path = os.path.join(DATA_PATH, replicated_csv_name)\nreplicated_df = pd.read_csv(replicated_csv_path)\n```\nThis notebook code (from `hosny_results_comparison.ipynb`) shows that the main comparison analysis loads a precomputed CSV rather than reproducing all upstream steps within the notebook itself. While providing cached outputs is useful for convenience, it weakens the paper’s “end-to-end” reproducibility framing unless the paper clearly separates “inspectable analysis” from “fully rerunnable pipeline from raw data.” In this setting, a reader can reproduce downstream plots/statistics but not necessarily reproduce the generated logits without running the full (hours-long) inference notebook and matching the exact environment. The manuscript describes that “each step” can be reproduced, but the primary evidence figure is driven by a file load of precomputed results. This increases the importance of strict environment pinning and provenance tracking for that CSV, which is not fully provided. Consequently, the artifact does not fully satisfy common reproducible computational research expectations.\n“In order to exactly reproduce a given result, it may be necessary to use programs in the exact versions used originally.” [[3]](#cite3)\nThis rule from a widely cited reproducible computational research guideline directly motivates why the paper’s unpinned dependencies and unpinned container pull are problematic. The manuscript’s goal is to demonstrate reproducibility in medical imaging pipelines, where version drift is a common failure mode. Yet the released environment specifications do not ensure that the “exact versions used originally” will be recovered in future reruns. This means that the paper’s practical recipe may not deliver the reproducibility benefits it advocates. The quote supports the critique that the authors should freeze versions (packages, OS image, GPU stack) to align artifact practice with reproducibility norms. Without doing so, the paper’s methodology does not meet its own stated objectives.\n\nReferences:\n[3] [Sandve GK, Nekrutenko A, Taylor J, Hovig E. “Ten Simple Rules for Reproducible Computational Research.” *PLOS Computational Biology* (2013).](https://journals.plos.org/ploscompbiol/article?id=10.1371/journal.pcbi.1003285)\n[4] [Docker Docs. “Tags on Docker Hub.”](https://docs.docker.com/docker-hub/repos/manage/hub-images/tags/)\n[5] [Chainguard Academy. “How to Sign an SBOM with Cosign.”](https://edu.chainguard.dev/open-source/sigstore/cosign/how-to-sign-an-sbom-with-cosign/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|44|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb44", "comment": "The paper proposes Google Colab as a solution for reproducibility, but fails to address the inherent instability of such platforms, which undermines the long-term reproducibility of the proposed pipelines.\n\n\"Hosny et Al. model was developed using Keras 1.2.2 and an old version of Tensorflow... Since early 2023, Google Colab instances are running TensorFlow 2.x.x only - and Hosny et Al. model is not compatible... Therefore, pulling the model from the project repository will not work.\"\nThe authors explicitly admit that the platform they advocate for (Google Colab) introduced a breaking change that rendered the original model unusable without significant modification (conversion to ONNX). This demonstrates that relying on managed cloud environments, which frequently update their underlying software stacks without user control, is detrimental to long-term reproducibility. A more robust approach would involve containerization (e.g., Docker) [1], which allows researchers to freeze the entire software environment, ensuring that the code runs indefinitely regardless of external platform updates. By not discussing containerization as a primary or alternative solution, the paper promotes a method that is susceptible to \"software rot.\"\n\nReferences:\n[1] Boettiger, C. (2015). An introduction to Docker for reproducible research. *ACM SIGOPS Operating Systems Review*, 49(1), 71-79. https://doi.org/10.1145/2723872.2723882", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|44|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb44", "comment": "The paper validates the reproduced pipeline on an unexplained \"subset\" of the original dataset, which compromises the statistical validity and comparability of the results.\n\n\"we compared our cloud-based pipeline with the original results shared by Hosny et Al. on a subset of the NSCLC-Radiomics dataset\"\nThe authors state they used a \"subset\" of the NSCLC-Radiomics dataset but fail to define how this subset was selected (e.g., random sampling, exclusion criteria, or data availability issues). Without this information, it is impossible to determine if the subset is representative of the full cohort used in the original study [2]. If the subset was chosen based on convenience (e.g., only cases available in IDC), it introduces potential selection bias. Furthermore, comparing performance metrics (AUC) derived from a subset against metrics derived from a different (likely larger) set in the original study is methodologically unsound unless the original study also reported results for this specific subset.\n\nReferences:\n[2] Hosny, A., Parmar, C., Quackenbush, J., Schwartz, L. H., & Aerts, H. J. (2018). Deep learning for lung cancer prognostication: A retrospective multi-cohort radiomics study. *PLoS Medicine*, 15(11), e1002711. https://doi.org/10.1371/journal.pmed.1002711", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|44|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb44", "comment": "The paper claims to demonstrate \"Pipelines\" (plural) for medical imaging, but the manuscript only presents a single case study, which is insufficient to support the broad claims of the title and abstract.\n\n\"Transparent and Reproducible AI-based Medical Imaging Pipelines Using the Cloud\" (Title)\nThe title and abstract use the plural \"Pipelines,\" implying a generalized framework validated across multiple scenarios. However, the text only describes the re-implementation of a single study by Hosny et al. [2]. While the accompanying code repository appears to contain a second study (Pai et al. [3]), this work is not discussed, analyzed, or even mentioned in the main text of the manuscript. A single example is not sufficient to claim a generalized solution for the diverse field of medical imaging, which involves various modalities, data formats, and preprocessing requirements. The manuscript should either include the second study to justify the plural or narrow its scope to a specific case study.\n\nReferences:\n[2] Hosny, A., Parmar, C., Quackenbush, J., Schwartz, L. H., & Aerts, H. J. (2018). Deep learning for lung cancer prognostication: A retrospective multi-cohort radiomics study. *PLoS Medicine*, 15(11), e1002711. https://doi.org/10.1371/journal.pmed.1002711\n[3] Pai, S., Bontempi, D., Prudente, V., Hadzic, I., Sokač, M., Chaunzwa, T. L., ... & Aerts, H. J. (2024). Foundation model for cancer imaging biomarkers. *Nature Machine Intelligence*, 6, 354–367. https://doi.org/10.1038/s42256-024-00806-z", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|44|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb44", "comment": "The paper advocates for uploading medical imaging data to commercial cloud platforms without a sufficient analysis of the privacy implications and cost barriers, which are critical factors in medical research.\n\n\"In the case of platforms such as the IDC, this process may constitute a challenge for a number of users, as additional steps for anonymization and institutional approval may be required to dismiss security and privacy concerns\"\nWhile the authors briefly acknowledge privacy concerns, they do not provide a detailed analysis or solution for how researchers should handle sensitive patient data (PHI) when using public cloud services like Google Cloud. In many jurisdictions (e.g., under GDPR or HIPAA), uploading patient data to a third-party commercial cloud is strictly regulated or prohibited [4]. Furthermore, the paper suggests that cloud resources are \"free to use\" (referring to Colab's free tier), but fails to address the significant costs associated with storage and compute for large-scale medical imaging datasets in a production or large-cohort research setting. Ignoring these practical barriers limits the applicability of the proposed framework.\n\nReferences:\n[4] Dove, E. S., Joly, Y., Tassé, A. M., & Knoppers, B. M. (2015). Genomic cloud computing: legal and ethical points to consider. *European Journal of Human Genetics*, 23(10), 1271-1278. https://doi.org/10.1038/ejhg.2014.296", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|44|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb44", "comment": "Who are the people that should follow the proposals in the manuscript and how are the authors planning to convince a critical mass of scientists to adopt their proposals? Without reaching critical mass, the proposed ideas will fail to deliver the sold benefits (since it would just be one of the many different and heterogeneous ways of openly providing reproducible pipelines).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|44|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb44", "comment": "After looking at Hosny et al. (the pipeline reimplemented by the authors), I wondered: how much time would it really save me to familiarize myself with the reimplementation instead of re-running the original pipeline by Hosny et al. Also, they provide links to the data and to a code repository. Can the advantage be quantified? How big is the advantage for other medical pipelines?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|44|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb44", "comment": "If, instead of proposing to use the Google Colaboratory, the authors would propose a common compute environment and set of (suggested) dependencies, wouldn’t the set of advantages be essentially the same? Still, not depending on the environment and dependency constraints set up by the third party (Google), everyone who develops for this common environment enables a similarly convenient way to reproduce their work. Of course, someone would have to keep this joint environment up-to-date, but it stands to reason that Google’s decisions (which are drawn from considerations that might be orthogonal to the ones relevant for the medical community) are less optimal than the ones the community itself would make.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|44|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb44", "comment": "In summary, I am left to wonder if the advantages of committing to using a third-party hard- and software stack is the right way to go for a field. Yes, committing to a common environment removes the overheads of heterogeneity, but it can also be constraining and comes with the danger of making oneself dependent on decisions the third party draws (problems as the ones eloquently enumerated in the manuscript). The manuscript contains one rather obvious idea, demonstrated on a single example pipeline. Other published work of similar nature exists but adds additional value to readers/users by providing reimplementations of many very useful computational AI modules [1].\\n\\nAt the same time, other approaches [2,3] to making AI modules themselves reproducible (independent from the surrounding pipeline). At the very least I would have hoped to see the AI parts in the presented work to pick up such alternative efforts.\\n\\nPersonally, I don’t see sufficient novelty to justify publication. Even worse, I remain with the belief that the benefits are much out-weight by the dangers of making an entire (sub-)community reliant on the uncontrollable decisions of a third party (Google).\\n\\n***References:***\\n\\n[1] https://www.nature.com/articles/s41467-021-22518-0\\n\\n[2] https://monai.io/model-zoo.html\\n\\n[3] [https://bioimage.io/](https://bioimage.io/#/) - https://www.biorxiv.org/content/10.1101/2022.06.07.495102v1", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|44|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb44", "comment": "While this proposition is not novel and has been previously suggested, its widespread adoption remains limited, perhaps due to a lack of systematic evidence. The authors recognize this gap in the existing literature and strive to investigate it, which is commendable.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|44|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb44", "comment": "The authors do not sufficiently discuss the limitations of their approach. For example, in my experience leading a large research group focusing on medical imaging analysis, we have found that most PhD students, even those proficient in computer science, prefer downloading data to a local machine. This preference stems from the flexibility and freedom offered by local computing, allowing the immediate application of the latest tools and methodologies. The administrative and logistical burdens associated with cloud-based computing, such as writing proposals and waiting for approvals, inhibit rapid experimentation and innovation, which are essential in our fast-paced research environment.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|44|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb44", "comment": "The authors have also neglected to consider two additional significant limitations. Firstly, the immense data requirements of certain medical image analysis problems, as illustrated by the UK Biobank’s dealing with 50,000 brain MRI images, often exceed the practical capabilities of conventional cloud-based resources. Secondly, and perhaps most crucially, they have not fully recognized the institutional reluctance to share medical data via cloud platforms. This resistance often necessitates data to remain on-premise, making an approach such as federated learning more viable. This should be discussed.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|44|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb44", "comment": "It could be interesting for the reader to have access to a list of potential alternative tools to Google Collaboratory, highlighting the most important key features of such platforms that are required to develop the proposed approach for AI pipelines documentation and management.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|44|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb44", "comment": "Mention and refer to the applicability of the proposed cloud-based approach when using synthetic data or differential privacy approaches applied on existing private datasets, which are increasing a frequent data context guarantying a better level of privacy for patients.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|44|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb44", "comment": "Nevertheless, beyond the use of appropriated tools, such as cloud-based solutions as described in the article, other reasons could have been mentioned for this lack of transparency, such as:\\n\\n- Question of Intellectual Property Rights (IPR) on development of new AI models (especially in the case of models aimed to exploited in a commercial manner\\n\\n- Ai for healthcare is a very competitive market, and most of the AI models developers for medical imaging face a challenge of speed of development and deployment. They might be reluctant to transparency in order to keep their competitive advantage. Most of the AI researchers/engineers teams are requested to “go fast” and so don’t take time to make available all information for transparency and reproducibility\\n\\n- Also, as a large part of current AI research in medical imaging are driven and funded by industry players, the researchers might not be authorized to publish everything.\\n\\n- Many startups are currently developing AI models for medical imaging and their R&D teams might not be compliant with the mentioned Ai development guidelines because of their lack of knowledge or experience on these guidelines.\\n\\n- The clients on this market (radiologists) are not very demanding in terms of scientific proofs and transparency/reproducibility so the developers are not prioritizing the tasks enabling full transparency and reproducibility.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|45|GPT|1", "source": "prb", "split": "test", "paper_id": "prb45", "comment": "This paper’s central thermodynamic framing (Validity; Conclusions) is compromised because the production simulations used to support phosphorylation patterns and condensate dissolution omit the dephosphorylation/reservoir-exchange mechanism needed to realize a non-equilibrium steady state (NESS), even though the manuscript repeatedly frames the method and verification as NESS/local-detailed-balance.\n\n“Importantly, we show how to verify by Markov-state modeling that the realisation of a non-equilibrium steady state satisfies local-detailed balance.”\nThis sentence frames the method as producing and validating a NESS, which implies a time-independent stationary distribution and stationary fluxes. However, the later Methods explicitly distinguish “validation simulations” (with an added reservoir-exchange step) from the main “dilute” and “condensate” simulations. Without a reverse pathway (dephosphorylation or reservoir exchange), the system is driven toward an absorbing, fully phosphorylated state rather than maintaining steady turnover, so it is not a steady state in the stochastic-thermodynamics sense. Consequently, the paper’s key thermodynamic-consistency framing does not directly apply to the main simulation results that are used for biological interpretation. In the NESS literature, the steady-state assumption is not cosmetic: it determines whether cycle affinities, stationary currents, and related balance relations are well-defined. The mismatch undermines the validity of interpreting observed time courses (e.g., dissolution) as steady-state behavior.\n“For the dilute regime, 100 simulations with phosphorylation reaction step and without reservoir exchange step were run, 2×10^{8} MD steps long (2 μs in simulation time) for the case with 1 wild type TDP-43 LCD and 1 CK1δ folded-domain, 4×10^{8} MD steps long (4 μs in simulation time) both for the case with 1 averaged-interaction polymer and 1 CK1δ folded-domain and for the case with 1 wild type TDP-43 LCD and 1 full-length CK1δ.”\nThis sentence explicitly states that the dilute-regime production simulations exclude the reservoir exchange step. In such a setup, the number of phosphorylated sites monotonically increases until saturation (given the strong bias described later), meaning the distribution over phosphorylation states is time-dependent rather than stationary. That time dependence breaks the core requirement for calling the dynamics a NESS, which is a time-independent stationary distribution under time-independent driving. Because phosphorylation patterns and rates are extracted from these trajectories, the reported “rates” and ordering reflect transient kinetics toward saturation, not steady-state fluxes. This distinction matters because many thermodynamic checks (e.g., local detailed balance expressed via steady-state transition probabilities) are derived under stationarity assumptions. The manuscript does not show that the key biological simulations satisfy stationarity, so the thermodynamic consistency verified elsewhere cannot be assumed to transfer.\n“We also simulated a condensate of 200 TDP-43 LCD chains. We ran 4 simulations 5×10^{8} MD steps long (5 μs in simulation time) with phosphorylation steps without reservoir exchange step (as for the single chain simulations) in presence of 1,3 or 5 CK1δ folded-domain chains and of 1,2 or 3 full-length CK1δ chains.”\nThis sentence extends the same omission to the condensate simulations that underpin the headline “condensate dissolution” result. Without reservoir exchange or an explicit dephosphorylation channel, the system is necessarily evolving in time as phosphorylation accumulates, so it is not sampling a steady state of a driven cycle. The manuscript later averages time series across replicas and interprets dissolution thresholds (e.g., ~24% pSer) as if the process were governed by an ongoing driven balance, but the system is instead progressing toward a terminal phosphorylation state. In established stochastic-thermodynamics treatments, a chemically driven NESS requires chemostats (or reservoirs) that maintain constant driving while allowing cycles to repeat; otherwise only a transient relaxation is observed. Therefore, labeling these production trajectories as NESS-like risks overstating the generality and thermodynamic interpretability of the results.\n“In our validation simulations, we assume the exchange between TDP-43 and phosphorylated TDP-43 happens without chemical driving and with equilibrium concentrations, through another Metropolis-like step (reservoir exchange step).”\nThis quote shows that the authors understand that multiple cycles (and hence steady cycling) require an additional exchange mechanism. That mechanism is introduced only for the special “validation simulations” used to compute cycle affinities, not for the main simulations that support biological conclusions. Because the reservoir exchange step is the ingredient that makes cycles repeat, omitting it changes the qualitative class of dynamics (cyclic steady-state vs. one-way progression to saturation). As a result, the paper’s strongest thermodynamic claim (validated NESS with local detailed balance) is demonstrated in a simplified auxiliary setup but not in the setups that produce the main findings. In peer practice, thermodynamic-consistency claims need to be demonstrated on the same class of simulations used for conclusions, or the scope must be narrowed. Here, the scope is not narrowed, leading to a validity gap.\n“This exchange step mimics a larger reservoir of TDP-43 and phosphorylated TDP-43 and thus enables us to simulate multiple phosphorylation cycles on the level of a single enzyme and single substrate protein simulation.”\nThis sentence clarifies the functional role of the reservoir exchange step: it is what makes repeated cycles possible in the authors’ model. That is exactly the condition needed for a NESS interpretation of cycle affinities and local detailed balance, because sustained cycling requires both forward and reverse pathways (or an exchange mechanism) at the level of system states. The manuscript, however, excludes this exchange step from the dilute and condensate simulations used for most biological conclusions. Therefore, the “multiple phosphorylation cycles” regime used for thermodynamic validation is a different dynamical regime from the production simulations. In standard practice, thermodynamic-consistency checks should be performed on the same regime that supports the main conclusions, or else the scope of the thermodynamic claim must be restricted. Here, the explicit acknowledgment that the exchange step enables cycling makes the omission in production simulations especially consequential.\n“Third, if the external driving is time-independent the system will reach a non-equilibrium steady state (NESS).” [[1]](#ref1)\nThis standard statement clarifies that a NESS is defined by time-independent driving leading to a stationary distribution and steady currents. In the paper under review, the driving parameter Δμ_P is treated as fixed, but the system’s phosphorylation state is not held stationary in the production simulations because there is no balancing mechanism to keep phosphorylation turnover ongoing. The result is a driven transient rather than a NESS, even if Δμ_P is constant. This distinction is essential when interpreting cycle affinities and local detailed balance, which are derived for steady-state path ensembles or stationary Markov dynamics. Therefore, the manuscript’s repeated NESS framing of the main simulations is not supported by its own simulation protocol choices.\n\nReferences:\n[1] U. Seifert, “Stochastic thermodynamics, fluctuation theorems, and molecular machines,” arXiv:1205.4176 (2012). https://arxiv.org/pdf/1205.4176.pdf", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|45|GPT|2", "source": "prb", "split": "test", "paper_id": "prb45", "comment": "The paper’s quantitative and semi-quantitative conclusions about phosphorylation dynamics and condensate dissolution (Conclusions; Data and methodology) are not robust because phosphorylation is implemented as a Metropolis swap attempted at a fixed, arbitrary frequency with near-certain acceptance upon contact, making effective kinetics largely an artifact of the chosen attempt schedule and contact definition rather than enzyme-catalysis or reaction-limited physics.\n\n“In addition to the standard MD simulation, we added a Monte Carlo step to mimic the phosphorylation reaction. Every 200 steps of MD simulation, we check if one of the TDP-43 phosphosites is in contact with the active site of CK1δ, the area of the enzyme that catalyzes the reaction, identified with the residues Asp149, Phe150 and Gly151. The contact criterion is the following: the three distances between the TDP-43 phosphosite and the residues of the CK1δ active site must all be less than 1 nm; in case more than one phosphosite is in contact with the active site at the same time-step, only the closest one is taken into account. When a contact occurs, we try to switch the Ser in contact into pSer (or the opposite) with a Metropolis-like acceptance probability in Eq. [2].”\nThis quote specifies a discrete “reaction attempt clock” (every 200 MD steps) that is not tied to any experimentally grounded catalytic rate or barrier. Because the reaction attempt frequency is an external algorithmic parameter, the absolute phosphorylation rates in μs⁻¹ reported later necessarily depend on this choice, and changing it would rescale kinetics without changing underlying molecular interactions. In hybrid MD/MC schemes, such Monte Carlo move schedules generally sample a target stationary distribution (if designed appropriately) but do not define a physical time mapping unless calibrated; the manuscript does not provide such calibration. Therefore, interpreting simulated phosphorylation times and rates as kinetic quantities is methodologically fragile. The issue is amplified by the fact that only one site is attempted per check (“only the closest one is taken into account”), which couples kinetics to an arbitrary selection rule when multiple sites are in contact. Overall, this undermines the reliability of time-to-dissolution and per-residue kinetic rankings as physical predictions.\n“By contrast, the acceptance probability for the phosphorylation MC step for Ser residues once they are in contact is > 0.97 for the entire sequence and the variations in the acceptance probability of the phosphorylation step are not correlated with the variation of the phosphorylation rates (SI Fig. S8).”\nThis indicates that, conditional on satisfying the geometric contact criterion, phosphorylation is almost always accepted. That design makes phosphorylation effectively diffusion-/contact-limited in the model, so any heterogeneity in phosphorylation “rates” is driven primarily by how often residues satisfy the contact criterion and by the MC scheduling, not by chemistry or catalytic selectivity. In real kinases, site-specific kinetics can depend on local sequence motifs, catalytic competence, and conformational gating; a model with >97% acceptance once within a distance cutoff cannot represent reaction-limited regimes or realistic catalytic discrimination. The paper later interprets differences in rates and ordering as mechanistic consequences of sequence and charges, but with near-unity acceptance the model hard-codes that mechanism as “whatever binds/contacts gets phosphorylated.” This is not merely a modeling simplification; it changes what the computed “rates” mean and limits how far the conclusions can be generalized. The manuscript does not quantify sensitivity of key results to the MC attempt interval or contact cutoff, so robustness is not demonstrated.\n“Hyper-phosphorylated TDP-43 chains start to disassociate from the condensate, which appears almost entirely dissolved after 5 \\( \\mu s \\) of simulation time in the last snapshot.”\nThis sentence is used to support a concrete microsecond-scale kinetic narrative (“dissolved after 5 μs”). However, in the model the phosphorylation reaction is triggered by a periodic Monte Carlo attempt schedule and is accepted with very high probability once a geometric contact criterion is met. As a result, the time at which a given phosphorylation level (and thus dissolution) is reached is sensitive to algorithmic choices such as the MC attempt interval, the contact cutoff, and the coarse-grained dynamical parameters that govern encounter frequencies. The paper does not provide a mapping or calibration from its hybrid MD/MC time to experimental kinase turnover times, so “5 μs” cannot be interpreted as a physical prediction. Even if the qualitative trend (phosphorylation weakens condensates) is plausible, the reported dissolution time is not shown to be robust to reasonable alternative MC schedules. Therefore, the kinetic timescale component of the dissolution conclusion is insufficiently supported.\n“In every simulation, the condensate starts to lose TDP-43 chains when about 24-25% of Ser are phosphorylated.”\nThis sentence asserts a sharp “threshold” phosphorylation fraction for the onset of condensate loss, which the manuscript uses as a key mechanistic marker. Yet the phosphorylation fraction itself is generated by the same algorithm-dependent MC reaction schedule, and the path by which the system reaches that fraction is a driven transient (not a calibrated steady-state process). Because the condensate size and composition are changing during the protocol, the apparent threshold can also depend on the specific time course of phosphorylation (e.g., which residues are modified first) and on how often the algorithm attempts reactions while chains remain in the dense phase. The paper does not provide sensitivity analyses showing that the ~24–25% onset fraction is stable to changes in attempt frequency, contact definition, or thermostat parameters. In standard coarse-grained PTM studies, such thresholds are usually reported as qualitative trends unless a careful robustness analysis is performed. Without that robustness evidence, the claimed threshold is not reliable as a quantitative conclusion.\n“The dynamics resulting from the stochastic transitions between system states is ruled by the Makovian master equation ˙ pi = X j Wijpj. The rate matrix, which may depend on time due to the external driving, satisfies P i Wij = 0 and is assumed ir-reducible.” [[2]](#ref2)\nThis literature statement highlights that kinetic predictions in stochastic thermodynamics hinge on well-defined transition rates (a rate matrix). In the present manuscript, the effective phosphorylation “rates” are not derived from a physical rate model; they are induced by periodically attempting Metropolis swaps at a chosen frequency. That choice effectively defines a rate matrix for phosphorylation attempts that is external to the molecular model and could be changed without changing the interaction potential. Without an explicit mapping from “every 200 MD steps” to an experimentally grounded catalytic attempt rate, the inferred μs⁻¹ phosphorylation rates cannot be compared quantitatively to real kinase kinetics. Moreover, when the acceptance probability is near unity, the effective rate matrix is dominated by contact statistics rather than reaction energetics. This mismatch between rate-definition requirements and the implementation weakens the methodological basis for kinetic claims.\n“To study the effect of PTMs on LLPS in silico, we extend our transferable coarse-grained model of intrinsically disordered proteins to include phosphorylated and acetylated amino acids.” [[5]](#ref5)\nThis sentence exemplifies a common scope for coarse-grained PTM modeling in the condensate literature: capturing how modifications change chain properties and phase behavior, not predicting enzyme-catalysis kinetics on an absolute time axis. The PTM model cited here treats modified residues via parameterized interaction changes, which is well-suited for thermodynamic and structural predictions but typically does not claim calibrated reaction times. In the manuscript under review, by contrast, the phosphorylation chemistry is implemented as a scheduled Metropolis swap and then interpreted in terms of microsecond-scale rates and dissolution times. The contrast underscores why kinetic claims require extra care: algorithmic choices can dominate the apparent “rate,” whereas thermodynamic trends can be robust. The paper would be on stronger ground if it presented dissolution and ordering primarily as thermodynamic/structural consequences of phosphorylation level rather than as time-calibrated kinetics. As written, the kinetic interpretation is not aligned with common practice in comparable coarse-grained PTM studies.\n\nReferences:\n[2] M. Esposito, “Stochastic thermodynamics under coarse-graining,” arXiv:1112.5410 (2011). https://arxiv.org/pdf/1112.5410.pdf\n[5] T. M. Perdikari, N. Jovic, G. L. Dignon, Y. C. Kim, N. L. Fawzi, and J. Mittal, “A predictive coarse-grained model for position-specific effects of post-translational modifications,” *Biophysical Journal* 120(7):1187–1197 (2021). https://pmc.ncbi.nlm.nih.gov/articles/PMC8059201/", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|45|GPT|3", "source": "prb", "split": "test", "paper_id": "prb45", "comment": "The paper’s thermodynamic-consistency validation (Validity; Conclusions) is incomplete because demonstrating \\(\\Delta\\mu_{\\text{cycle}} \\approx \\Delta\\mu_P\\) on a highly coarse-grained 3–4 state MSM is not, by itself, a rigorous verification of local detailed balance or of total entropy production in the underlying driven MD/MC dynamics, especially given known hidden-entropy-production issues under coarse-graining.\n\n“The first step is to validate the thermodynamic consistency of our simulations by showing that the energy gain in a phosphorylation cycle (referred to as \\( \\Delta \\mu_{cycle} \\) in the following) is equal to the chemical potential difference \\( \\Delta \\mu_P \\) in the phosphorylation step.”\nThis sentence sets a strong validation goal: thermodynamic consistency of the driven simulations. However, the proposed validation compares a quantity computed from a coarse-grained MSM cycle to an input parameter (Δμ_P) that is explicitly inserted into the Metropolis acceptance rule. Because Δμ_P is directly used to bias the forward/backward reaction move, agreement between an inferred cycle affinity and Δμ_P is not an independent check; it can occur even if other sources of entropy production are present or if coarse-graining hides dissipation. In stochastic thermodynamics, local detailed balance is a constraint on microscopic transition rates/noise, not merely on an arbitrarily aggregated state model. The MSM construction involves state definitions (bound/unbound; Ser/pSer) and a chosen lag time, which can affect inferred transition probabilities and hence inferred affinities. Therefore, the presented equality is at best a partial sanity check of implementation, not a sufficient proof of overall thermodynamic consistency.\n“If our system is a NESS, the local detailed balance condition must be satisfied [3], [5]: \\[ \\Delta \\mu_{cycle} = -k_B T \\ln \\left( \\frac{T_{12}T_{23}T_{34}T_{41}}{T_{14}T_{43}T_{32}T_{21}} \\right) \\]”\nThis quote equates a coarse-grained cycle affinity computed from MSM transition probabilities with “the local detailed balance condition.” In standard stochastic thermodynamics, “local detailed balance” refers to a microscopic constraint on transition rates/noise that ensures consistent identification of entropy flow and production; it is not automatically preserved under coarse-graining. The manuscript’s MSM lumps vast sets of configurations into just four states; such aggregation can introduce hidden entropy production and can make apparent affinities depend on the state definition and lag time, even when microscopic dynamics are consistent. While cycle-affinity estimation is meaningful, calling it “local detailed balance” at the MSM level risks conflating a macroscopic-cycle identity with a microscopic constraint. In addition, the paper assumes without direct demonstration that non-reaction transitions satisfy detailed balance in the coupled MD/MC dynamics, which is not guaranteed after coarse-graining and time discretization. As a result, the presented equation does not by itself establish that the simulation realizes a thermodynamically consistent NESS at the microscopic level.\n“For a basic Markovian dynamics implemented either on the continuum level with Langevin equations or on a discrete set of states as a master equation, thermodynamic consistency imposes a local-detailed balance constraint on noise and rates, respectively.” [[1]](#ref1)\nThis review statement clarifies that local detailed balance is fundamentally a constraint on microscopic stochastic dynamics (noise in Langevin dynamics or rates in master equations). The paper under review does not directly demonstrate that its coupled MD/MC dynamics satisfies this constraint at the microscopic move level (e.g., by relating forward/backward microscopic move probabilities to heat/chemical work). Instead, it evaluates an affinity on a coarse MSM built from observed transitions. That approach can be informative, but it is not equivalent to verifying the microscopic local-detailed-balance constraint that ensures correct entropy accounting. Therefore, citing “local detailed balance” while only checking a coarse-grained MSM affinity is a methodological overreach. A more standard approach would either (i) compute entropy production from microscopic move statistics and compare to applied affinities, or (ii) demonstrate coarse-graining invariance of inferred affinities and hidden dissipation bounds.\n“This leads to the important result that neglecting any of these contributions will always imply an underestimation of entropy production.” [[2]](#ref2)\nThis statement directly cautions that coarse-graining can hide (and thus underestimate) entropy production. The MSM used in the paper is an extreme coarse-graining (few macrostates), which makes hidden dissipation a real concern if one wants to claim thermodynamic consistency of the underlying process rather than of the coarse model alone. Even if the MSM cycle affinity matches Δμ_P, additional entropy production can exist in unresolved degrees of freedom (e.g., within the bound ensemble, within conformational substates, or due to time discretization), which the MSM will not capture. The manuscript does not bound or estimate such hidden contributions, nor does it show that the MSM coarse-graining is “thermodynamically closed.” As a result, the thermodynamic-consistency claim is not established at the level implied by the paper’s framing. This is a major issue because the paper motivates its approach partly by the difficulty of verifying thermodynamic consistency of driven simulations.\n“We also present an efficient estimator for reversible transition matrices and a robust test to validate that a MSM reproduces the kinetics of the molecular dynamics data.” [[3]](#ref3)\nThis sentence emphasizes that MSM validation is about reproducing kinetics of the underlying data, and that robust validation tests are needed. In the manuscript under review, Chapman–Kolmogorov tests are shown for some cases, but the thermodynamic claim requires more than kinetic Markovianity: it requires correct entropy accounting under driving. A kinetically valid MSM can still miss entropy production under coarse-graining, as noted above. Therefore, standard MSM validation criteria do not automatically imply thermodynamic consistency of the underlying non-equilibrium process. The paper would need to connect MSM validation to entropy-production completeness or to show that relevant thermodynamic currents are resolved by the state space. Without that, the presented MSM checks are insufficient for the thermodynamic conclusions claimed.\n\nReferences:\n[1] U. Seifert, “Stochastic thermodynamics, fluctuation theorems, and molecular machines,” arXiv:1205.4176 (2012). https://arxiv.org/pdf/1205.4176.pdf\n[2] M. Esposito, “Stochastic thermodynamics under coarse-graining,” arXiv:1112.5410 (2011). https://arxiv.org/pdf/1112.5410.pdf\n[3] J.-H. Prinz, H. Wu, M. Sarich, B. Keller, M. Senne, M. Held, J. D. Chodera, C. Schütte, and F. Noé, “Markov models of molecular kinetics: generation and validation,” *J. Chem. Phys.* 134, 174105 (2011). https://pubmed.ncbi.nlm.nih.gov/21548671/\n[5] T. M. Perdikari, N. Jovic, G. L. Dignon, Y. C. Kim, N. L. Fawzi, and J. Mittal, “A predictive coarse-grained model for position-specific effects of post-translational modifications,” *Biophysical Journal* 120(7):1187–1197 (2021). https://pmc.ncbi.nlm.nih.gov/articles/PMC8059201/", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|45|GPT|4", "source": "prb", "split": "test", "paper_id": "prb45", "comment": "The manuscript’s residue-level phosphorylation-rate estimates and inferred ordering (Conclusions; Appropriate use of statistics and treatment of uncertainties) are not statistically robust because they rely on single-event-per-residue data and a single-exponential assumption that the authors themselves note is violated for key sites.\n\n“To estimate the phosphorylation rates \\( r_p \\), we assume that the phosphorylation process is a memory-less process, which follows single-exponential kinetics [55]. In this case, observing a single event is in principle sufficient to estimate the rates of a process.”\nThis quote makes the statistical assumption and its justification explicit. While a single-event likelihood can, in principle, inform a Poisson rate under strong modeling assumptions, the resulting uncertainty is typically large and highly sensitive to censoring and to deviations from the assumed hazard model. Here, phosphorylation is explicitly conditional on binding/contact events, and the paper later argues that prior phosphorylation can change binding and thus alter subsequent rates, which violates a memoryless single-exponential model. The manuscript reports per-residue rates with fine differences (e.g., 2–10% differences between models for some sites), but those differences are hard to trust when the underlying statistical model is only approximately satisfied. Moreover, single-event sufficiency is a statement about identifiability under the assumed model, not about practical precision or robustness under model misspecification. In standard practice, rate estimation for rare events typically requires either many events or a validated kinetic model that accounts for competing processes and conditioning; the manuscript does not provide that level of validation.\n“In all the collected 100 simulations, we had at most one phosphorylation event for each Ser residue, happening at time \\( t_P^i < t_{tot} \\) for simulation \\( i \\), with \\( t_{tot} \\) the total time of the simulation.”\nThis quote shows that the dataset for each residue is extremely sparse (zero or one event per trajectory). Such sparsity makes rate estimates highly sensitive to trajectory length, censoring, and any heterogeneity across simulations (e.g., varying encounter histories). It also makes it difficult to detect and model multi-step kinetics, which the manuscript later suggests may be present for some residues. Because the authors then use these estimated rates to draw mechanistic conclusions (sequence context, charge effects, and differences between residues), the limited event counts create a major uncertainty bottleneck. The paper does report some uncertainties, but with one event per run the uncertainty structure is dominated by the modeling assumptions rather than empirical repetition. In this setting, showing robustness to alternative hazard models or to different conditioning (e.g., time spent bound vs. total time) would be expected for strong kinetic claims.\n“These comparison suggests that the phosphorylation of Ser 403 and Ser 407 could actually follow a more complex process.”\nThis is an internal acknowledgment that the single-exponential model may not hold for at least some key residues. Ser403 and Ser407 are central to the paper’s biological narrative (e.g., sites discussed as prominent and disease-linked), so model misspecification here directly impacts conclusions about site preference and sequence determinants. If phosphorylation kinetics are more complex (e.g., due to phosphorylation-dependent binding changes), then reporting single-exponential rates as residue-intrinsic properties is potentially misleading. The manuscript proceeds to compute probabilities of ordering and interpret patterns mechanistically, but those downstream analyses implicitly assume comparability and stability of the per-residue kinetic descriptors. A more rigorous approach would explicitly model state-dependent rates (e.g., conditional on current phosphorylation count) and propagate uncertainty. As written, the manuscript’s own caveat indicates the statistical model may be inadequate for the claims being made.\n“This approach has many appealing characteristics compared to straightforward molecular dynamics simulation and analysis, including the potential to mitigate the sampling problem by extracting long-time kinetic information from short trajectories and the ability to straightforwardly calculate expectation values and statistical uncertainties of various stationary and dynamical molecular observables.” [[3]](#ref3)\nThis statement summarizes why MSM-style kinetic modeling is widely used: it provides a principled way to compute observables and uncertainties when the modeling assumptions are satisfied and sampling is sufficient. In the manuscript under review, however, the phosphorylation-rate estimates are not derived from a state-resolved kinetic model; they are derived from sparse event timing under a simple hazard assumption. Given the acknowledged possibility of multi-step kinetics and phosphorylation-dependent binding, a more standard approach would be to construct a kinetic model with state-dependent hazards (or an MSM/HMM capturing gating) and then report rates with uncertainty that reflects both sampling and model error. The current approach instead collapses potentially state-dependent kinetics into single numbers per residue, likely underestimating uncertainty and obscuring mechanism. Therefore, relative-rate comparisons and fine-grained ordering conclusions should be treated as insufficiently supported.\n\nReferences:\n[3] J.-H. Prinz, H. Wu, M. Sarich, B. Keller, M. Senne, M. Held, J. D. Chodera, C. Schütte, and F. Noé, “Markov models of molecular kinetics: generation and validation,” *J. Chem. Phys.* 134, 174105 (2011). https://pubmed.ncbi.nlm.nih.gov/21548671/", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|45|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb45", "comment": "The description of the MC component is not sufficiently clear. For example, if I understand correctly, \\( \\Delta \\mu P \\) controls only the relative magnitudes of k_{23} and k_{32} (or the transition probabilities T_{23} and T_{32}). On what basis are the absolute values of these quantities set? How do their absolute values affect the entire MC + MD cycle? Additionally, in Figure 1, there are arrows with different lengths and thicknesses. Do they signify different meanings? For instance, the arrow representing k_{23} is thicker than the others; does this indicate that k_{23} is significantly larger than the others?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|45|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb45", "comment": "It is surprising that the “averaged interaction” leads to a difference of an order of magnitude in contact probability compared to the wild type. According to the description in Line 496, I expected to find the averaged values of the parameters in the Supporting Information, but they are absent. The authors should provide a direct description of these parameters in the main text.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|45|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb45", "comment": "The last paragraph on Page 7 suggests that the positive charges in the N-terminus determine the differences in phosphorylation rates between the N- and C-termini. However, the first paragraph on Page 11 indicates that even without considering the specific charge distribution, the C-terminal serine residues still exhibit higher phosphorylation rates. Are these two statements contradictory? Which factor plays a more decisive role in determining the phosphorylation rate—the charge pattern or the serine sequence pattern?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|45|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb45", "comment": "It is interesting to observe that in simulations with a single enzyme and a single TDP43 molecule, binding and unbinding processes occur, whereas in droplet simulations, the enzyme (without the disordered tail) mainly binds on the surface of the condensate (Figure 4). In this case, is the primary contribution to the interaction between the enzyme and TDP43 from LJ or electrostatic interactions? Why does the enzyme remain on the surface rather than entering the interior of the TDP43 condensate?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|45|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb45", "comment": "After phosphorylation, does TDP43 redistribute within the condensate? Do phosphorylated sites remain on the surface? Does this affect the “saturation” of the phosphorylation rate? The authors mention that the overall phosphorylation percentage starts to induce dissolution when it reaches 24%. For each individual chain, at what phosphorylation percentage does it migrate into the dilute phase?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|45|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb45", "comment": "The authors found that enzymes mainly bind to the surface of the condensates, even when the migration of phosphorylated TDP43 from the condensate was observed (Figure 4). However, it was also claimed that phosphorylation increases the binding affinity between TDP43 and the enzyme (Page 10). In this sense, shouldn’t the enzyme be more strongly attracted to phosphorylated TDP43 in the dilute phase?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|45|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb45", "comment": "While ATP and ADP are modeled implicitly, the concentrations of these molecules may also affect phase separation (D Kota, ..., HX Zhou. 2024. JACS 146, 1326; M Dang, ..., J Song. 2021. Commun Biol 4, 714). The authors should discuss this point to provide a more comprehensive understanding.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|45|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb45", "comment": "Figure 2c: The description of the colored dots and lines is missing. Please include a legend or description to clarify what they represent.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|45|Human_1|10", "source": "prb", "split": "test", "paper_id": "prb45", "comment": "Line 143: Consider changing \"goodness\" to \"reliability\" to enhance clarity.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|45|Human_1|11", "source": "prb", "split": "test", "paper_id": "prb45", "comment": "Figure 3f: The thickness of the arrows pointing from \"np\" to \"pS410\" indicates the percentage. How about the arrows connecting \"np\" and \"(n+1)p\"? If they have a different meaning, consider using a different drawing style. Also, please include a detailed explanation in the figure caption.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|45|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb45", "comment": "Could the authors comment on how phosphorylation patterns found in patient samples may be mechanistically linked to the disruption of condensate formation? Given that understanding the pathological role of phosphorylation in TDP-43 is central to this work, a brief discussion—even speculative—would help frame the broader implications of these findings.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|45|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb45", "comment": "There have been recent reports correlating TDP-43 phase separation with functional aspects of the protein (e.g., bioRxiv, DOI: 10.1101/2024.07.05.602258). Can the authors clarify whether similar functionality-related effects of phase separation are being modeled here, or is this system reflecting a more complex behavior specific to TDP-43?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|45|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb45", "comment": "While the model seems suitable for studying IDP phase behavior, it is less clear if it accurately represents interactions between TDP-43’s C-terminal domain and CK1δ. Could the authors discuss any limitations of their model in capturing these specific binding events?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|45|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb45", "comment": "As it is well known that TDP-43 CTD phase separation is driven by interactions mediated by its conserved helical region, the authors should comment on how they model this helical region. Additionally, how does the helical region factor into interactions with CK1δ and the resulting phosphorylation patterns?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|46|Claude|1", "source": "prb", "split": "test", "paper_id": "prb46", "comment": "The paper employs random shuffling followed by standard cross-validation for evaluating property prediction performance, rather than using scaffold-based or structure-aware splitting strategies that are now standard practice in molecular/polymer machine learning benchmarks.\n\n\"After shuffling, we split the data set into two parts and use 80% for the five cross-validation models and for validating the meta learners. 20% of the data set is used for training the meta learners. We perform data set stratification of all splits based on the polymer properties.\"\nThe paper explicitly describes using random shuffling followed by property-based stratification, but does not employ any structure-based splitting strategy. Stratification by property values does not prevent structurally similar polymers from appearing in both training and test sets. This is a significant methodological concern because when similar polymer structures appear in both sets, the model can achieve high performance by memorizing structural patterns rather than learning generalizable relationships. This approach may lead to optimistic performance estimates that do not reflect real-world generalization to novel polymer chemistries.\n\"For all the MoleculeNet datasets, we employed the scaffold splitting method. Scaffold splitting, which separates molecules based on their molecular substructures, i.e., scaffolds, offers a more rigorous evaluation of a model's ability to generalize to out-of-distribution samples compared to the normal random splitting.\" [[1]](#citation-list)\nThis quote from a recent molecular property prediction benchmark study explicitly states that scaffold splitting provides more rigorous evaluation than random splitting for assessing generalization. The MoleculeNet benchmark, which has become the standard for molecular machine learning evaluation, specifically uses scaffold splitting for this reason. The polyBERT paper's use of random splitting means its reported R² values (0.80-0.81) may not accurately reflect how well the model would perform on truly novel polymer structures that differ significantly from the training data.\n\"Data Leakage Analysis. To rigorously evaluate the degree of data leakage, we conducted a quantitative comparison between the random and scaffold splits... As visualized in Figure 3, the random split (red) exhibits high structural redundancy with a mean similarity of [high] and extensive coverage... In stark contrast, the scaffold split (blue) induces a significant distributional shift towards lower similarity.\" [[2]](#citation-list)\nThis analysis from a recent benchmark study quantitatively demonstrates that random splits allow substantial data leakage through structural similarity, while scaffold splits effectively minimize structural overlap between training and test sets. The polyBERT paper's exclusive use of random splitting without any quantitative analysis of structural overlap between splits means the reported performance metrics may be significantly inflated due to this data leakage phenomenon, undermining the validity of the comparison between polyBERT and Polymer Genome fingerprints.\n\nReferences:\n[1] [Topology-Aware Multiscale Mixture of Experts for Efficient Molecular Property Prediction](https://arxiv.org/html/2601.12637v1) - arXiv (2025)\n[2] [NMRGym: A Comprehensive Benchmark for Nuclear Magnetic Resonance](https://arxiv.org/html/2601.15763v1) - arXiv (2025)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|46|Claude|2", "source": "prb", "split": "test", "paper_id": "prb46", "comment": "The 100 million hypothetical polymers used to pre-train polyBERT are generated exclusively through BRICS decomposition and recombination of only 13,766 known polymers, which restricts the learned representations to the chemical space covered by combinations of existing fragments and may limit generalization to truly novel polymer chemistries.\n\n\"First, 13 766 known (i.e., previously synthesized) polymers are decomposed to 4 424 fragments using the BRICS method. Second, re-assembling the BRICS fragments in many different ways generates 100 million hypothetical polymers by randomly and enumeratively combining the fragments.\"\nWhile 100 million polymers sounds like a massive dataset, the underlying diversity is fundamentally constrained by only 4,424 unique fragments derived from existing polymers. This combinatorial approach cannot generate polymer structures containing novel functional groups, atom combinations, or bonding patterns that were not present in the original 13,766 polymers. Consequently, polyBERT learns the \"polymer chemical language\" only within the bounded vocabulary of known polymer chemistry, potentially limiting its ability to represent or predict properties of polymers with genuinely novel structural features.\n\"The hypothetical PSMILES strings are chemically valid polymers but, mostly, have never been synthesized before.\"\nWhile the authors acknowledge these are hypothetical polymers, they do not address the fundamental limitation that \"hypothetical\" in this context means novel combinations of existing building blocks rather than truly novel chemical structures. The model's chemical vocabulary is inherently limited to patterns that can be expressed using the 4,424 fragments, which may create blind spots for emerging polymer classes that incorporate new chemistry not represented in the original 13,766 synthesized polymers.\n\"The concentration bias makes the identification of novel active molecules in peripheral areas challenging, as the model receives insufficient training examples from these regions... uniformly with equal probability in the augmentation module, the generated molecules maintain a similar distribution pattern to the original training data.\" [[3]](#citation-list)\nThis observation from a recent study on molecular generation highlights how combinatorial approaches from existing data maintain similar distribution patterns to the original training data, creating concentration bias that limits exploration of peripheral chemical space. The polyBERT pre-training suffers from an analogous limitation—by generating 100 million polymers from only 4,424 fragments, the model is heavily biased toward the chemical space represented by the original 13,766 synthesized polymers, potentially limiting its utility for discovering polymers with unprecedented structural features.\n\nReferences:\n[3] [Scaffold-Aware Generative Augmentation and Reranking for Virtual Screening](https://arxiv.org/html/2510.16306v2) - arXiv (2024)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|46|Claude|4", "source": "prb", "split": "test", "paper_id": "prb46", "comment": "The paper's performance evaluation compares polyBERT exclusively against Polymer Genome fingerprints, without including other established molecular representation methods such as Morgan fingerprints, graph neural networks, or other transformer-based approaches that are commonly used as baselines in molecular property prediction studies.\n\n\"For benchmarking the property prediction accuracy of polyBERT and PG fingerprints, we train multitask deep neural networks for each property category defined in Table 1.\"\nThe paper frames the comparison as a benchmark but only includes one alternative method (Polymer Genome fingerprints). This limited comparison makes it difficult to assess whether polyBERT's performance advantages (speed) or disadvantages (slightly lower accuracy) are specific to this comparison or generalizable across different representation methods. A more comprehensive benchmark would include extended-connectivity fingerprints (ECFP/Morgan fingerprints), graph neural network representations, and other transformer-based molecular models.\n\"Overall, PG performs best (R² = 0.81) but is very closely followed by polyBERT (R² = 0.80).\"\nThe reported performance difference (0.01 in R²) is marginal and falls within typical experimental variation, yet no other baselines are provided to contextualize this comparison. Without comparing against Morgan fingerprints or other established methods commonly used in molecular property prediction benchmarks, it is unclear whether both methods are performing near the state-of-the-art or whether there is substantial room for improvement that other approaches might achieve.\n\"We compare our approach against six state-of-the-art polymer and molecular property prediction models... The evaluated baselines include polyBERT, TransPolymer, polyGNN, Mol-GDL, GEM, and Mol-TDL.\" [[1]](#citation-list)\nSubsequent studies evaluating polymer property prediction methods have established more comprehensive baselines that include multiple representation approaches. The polyBERT paper's limited comparison against only Polymer Genome fingerprints does not provide sufficient context to understand how the method performs relative to the broader landscape of available techniques, limiting the conclusions that can be drawn about the relative merits of the transformer-based approach.\n\nReferences:\n[1] [Topology-Aware Multiscale Mixture of Experts for Efficient Molecular Property Prediction](https://arxiv.org/html/2601.12637v1) - arXiv (2025)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|46|GPT|1", "source": "prb", "split": "test", "paper_id": "prb46", "comment": "The paper’s reported “meta learner” performance is not a valid estimate of generalization because the meta learner is evaluated on data that were used to train the underlying cross-validation predictors, which can leak information via in-fold predictions; this undermines the validity of the “exceptional prediction performance” claim for Figure 4b and downstream use of the meta learners.\n\n“We train the meta learners on unseen 20% of the data set and validate using 80% of the data set (also used for cross-validation). The reported validation \\(R^2\\) values thus only partly measure the generalization performance with respect to the full data set.”\nThis explicitly states the meta learner is validated on the same 80% portion that is used to fit the cross-validation models, meaning the meta learner’s inputs (the base-model predictions) can include predictions from models that were trained on the same datapoints they are predicting. In standard stacked generalization, the meta learner must be trained/evaluated only on out-of-fold predictions to avoid this “self-prediction” leakage. The authors’ own caveat (“only partly measure the generalization performance”) acknowledges that the reported \\(R^2\\) is not a clean generalization metric, but the paper still uses these meta learners “for all property predictions in this work,” making the issue central to their conclusions. Because Figure 4b is presented as “test” performance of the meta learner, readers may mistakenly interpret it as an unbiased holdout estimate. This compromises the reliability of the key accuracy claims tied to the meta learners.\n“After shuffling, we split the data set into two parts and use 80\\% for the five cross-validation models and for validating the meta learners. 20\\% of the data set is used for training the meta learners.”\nThis describes a stacking setup where the meta learner is validated on the same pool used to train the base predictors, which is the opposite of common leakage-avoiding practice (train base models on one fold and generate out-of-fold predictions for meta training/evaluation). In five-fold CV, for any datapoint in the 80% pool, four of the five CV models were trained on that datapoint, so their predictions can be unrealistically accurate even if they would generalize poorly to new polymers. Feeding those partially in-sample predictions into the meta learner makes it easy for the meta learner to achieve near-perfect parity plots and \\(R^2\\), without reflecting true out-of-sample performance. The paper does not describe any nested or grouped split that would prevent the same polymer (or closely related chemistries) from appearing in both “training” and “validation” contexts through the ensemble. As a result, the meta learner metrics are at high risk of optimistic bias.\n“Figure S2: Learning workflow. … **b** Meta learner. The meta learner includes the five multitask models (blue nodes) with fixed weights. The outputs of these five multitask models are the inputs to a feed-forward network (grey nodes).”\nThis confirms that the meta learner is trained on the base models’ outputs, i.e., a classic stacking/blending architecture where leakage is a well-known risk if the meta features are generated from models trained on the same samples. In such architectures, the correctness of the evaluation hinges on how those base-model outputs are generated for the meta learner (out-of-fold vs in-sample). Combined with the paper’s stated split (80% used to train base models and validate the meta learner), this diagram implies that the meta learner likely sees “too-easy” prediction features derived from in-sample base-model behavior. That mechanism can explain why the meta learner’s \\(R^2\\) values become extremely high compared to cross-validation, without necessarily improving real generalization. The paper does not provide a leakage-controlled protocol (e.g., cross_val_predict-only meta features) that would address this. Therefore, the meta learner results cannot be trusted as reported.\n“<tr><td>\\( T_g \\)</td><td>30.18±0.88</td><td><b>28.78±0.40</b></td><td>0.92±0.01</td><td><b>0.92±0.00</b></td><td>12.66</td><td>12.80</td><td><b>0.99</b></td><td>0.98</td></tr>”\nThis table row shows a dramatic jump from cross-validation \\(R^2\\approx 0.92\\) to meta learner \\(R^2\\approx 0.99\\) for the same property, which is suspiciously large for a mere “consolidation” step unless the meta learner is benefiting from information leakage or an evaluation artifact. A stacking meta learner can legitimately improve performance, but such near-perfect \\(R^2\\) across many properties (as shown throughout Table S1) is atypical in heterogeneous experimental polymer datasets, especially when the base models are far from perfect. The paper provides no evidence that these meta \\(R^2\\) values are computed on a strict held-out set that was not used in any way to train the base predictors producing the meta inputs. Given the split description, it is plausible that the meta learner is evaluated on in-sample-like predictions, inflating performance. This directly weakens the credibility of the paper’s “exceptional prediction performance” characterization.\n“Note that `estimators_` are fitted on the full `X` while `final_estimator_` is trained using cross-validated predictions of the base estimators using `cross_val_predict`. … Please note that if the models have been trained on the same data to train the stacking model, there is a very high risk of overfitting.” ([1](#ref1))\nThis widely used reference implementation of stacking states the key leakage-avoidance principle: the meta learner should be trained on cross-validated (out-of-fold) predictions, and it explicitly warns about a “very high risk of overfitting” when training the stacking model on predictions from models trained on the same data. The paper’s described protocol (validate meta learners on the same pool used to fit the CV models) is precisely the kind of setup that the documentation flags as risky. The warning is not a minor best-practice note; it is a statement that the evaluation can become invalid because the meta learner can exploit overfit signals present in in-sample predictions. Because the paper’s main downstream predictions for 100 million polymers rely on the meta learners, any inflation here propagates to the headline screening results. This directly supports the criticism that the reported meta learner \\(R^2\\) is not a reliable generalization estimate.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|46|GPT|2", "source": "prb", "split": "test", "paper_id": "prb46", "comment": "The paper’s interpretation of the minimum/maximum predicted values across 100 million hypothetical polymers as “potential boundaries” of polymer property space is not supported, because the hypothetical polymers are largely unsynthesized and may lie outside the supervised model’s applicability domain, yet the paper provides no uncertainty quantification or out-of-distribution validation to justify treating prediction extrema as physical/chemical bounds.\n\n“The hypothetical PSMILES strings are chemically valid polymers but, mostly, have never been synthesized before.”\nThis establishes that the 100 million candidates are predominantly unsynthesized, so their true properties are unknown and cannot be assumed to follow the same distribution as the labeled training data. Even if the strings are syntactically valid, “chemically valid” does not imply synthesizable, stable, or within the domain spanned by the supervised property dataset. Screening such a vast, mostly unverified space invites out-of-distribution (OOD) inputs where neural predictors can extrapolate unpredictably. In that setting, predicted extrema are especially sensitive to model misspecification and can be driven by artifacts rather than meaningful chemistry. Because the paper uses these candidates to make a strong claim about global property limits, the lack of a domain-of-applicability check becomes a critical validity gap. The paper does not show any empirical verification that the extremes correspond to plausible polymers.\n“Given the vast size of our data set and consequent chemical space of the 100 million hypothetical polymers, the minimum and maximum values can be interpreted as potential boundaries of the total polymer property space.”\nThis sentence makes a substantive scientific claim: that model-predicted extrema approximate boundaries of real polymer property space. However, statistical extrema from model predictions over a huge candidate set are not evidence of physical bounds unless the model is calibrated, validated under distribution shift, and constrained to an applicability domain where its errors are controlled. Extreme values are particularly prone to error because even small calibration biases can produce large errors at the tails, and the “winner’s curse” (selecting maxima over many samples) amplifies spurious extremes. The paper provides neither confidence intervals nor any uncertainty metric on these extrema, so there is no way to tell whether the predicted maxima/minima are robust. Without external validation or uncertainty-aware screening, interpreting extrema as “boundaries” overstates what the data support. This directly undermines a central conclusion of the large-scale screening component.\n“To assess robustness to dataset shift, we evaluate the predictive uncertainty on test examples from known and unknown distributions, and show that our method is able to express higher uncertainty on out-of-distribution examples.” ([2](#ref2))\nThis highlights a common practice in modern ML for scientific prediction: explicitly evaluating distribution shift and using uncertainty estimates to detect OOD inputs. The paper under review performs massive screening over largely unsynthesized polymers, which is exactly the scenario where dataset shift is expected and where uncertainty-aware methods are most relevant. Yet the paper does not report any uncertainty quantification (e.g., ensembles, Bayesian methods, conformal prediction) for the 100 million predictions, nor does it filter candidates based on uncertainty. Without such analysis, the reliability of the predicted extremes is unclear because the model may be least reliable precisely where it predicts the most extreme values. The cited work demonstrates that OOD-aware uncertainty is measurable and can be used to avoid overconfident extrapolation. The absence of any comparable analysis in the paper is therefore a significant methodological omission.\n“For an acceptable (Q)SAR prediction, the input must be correct, the substance fall within the applicability domain of the model, the prediction be reliable and the outcome fit for the regulatory purpose.” ([3](#ref3))\nThis guidance articulates a broadly accepted principle in quantitative structure–activity/property modeling: predictions are only defensible when the input lies within the model’s applicability domain and reliability is established. The paper’s “property boundaries” claim implicitly assumes that all 100 million hypothetical polymers fall within the trained predictor’s domain, but it provides no evidence or criterion for that assumption. It also assumes that predicted extrema remain reliable, yet applicability-domain violations are most common for unusual chemistries that may drive extreme predictions. The guidance further stresses that “fit for the regulatory purpose” depends on reliability, which here would correspond to making claims about global bounds. Without demonstrating applicability-domain coverage and reliability, the inference from predicted extrema to physical boundaries is not warranted. This directly contradicts the paper’s strong interpretation of min/max predictions.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|46|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb46", "comment": "The paper reports performance metrics for the \"meta-learner\" that are likely based on training data or suffer from data leakage, resulting in unrealistically high accuracy scores that do not reflect true generalization capability.\n\n\"Meta learner RMSE and R2 values for 29 polymer properties\" (Table S1 caption)\nThe table reports \"Meta\" R2 values of 0.99, 0.98, 0.96 for properties where the cross-validation (CV) performance of the base models is significantly lower (e.g., Td CV R2 is 0.70, but Meta R2 is 0.96). Such a massive improvement (reducing error variance by ~87%) by simply stacking correlated models is statistically implausible on unseen data.\n\"The meta learner includes the five multitask models (blue nodes) with fixed weights. The outputs of these five multitask models are the inputs to a feed-forward network (grey nodes).\" (Figure S2 caption)\nThis architecture describes a stacking ensemble. Standard practice for stacking requires the meta-learner to be evaluated on a held-out test set that was not used to generate the input predictions (or using nested cross-validation). The reported metrics, being near-perfect, strongly suggest the meta-learner was evaluated on the same data used to train it (the out-of-fold predictions of the base models), which constitutes training error, not test error.\n\"Stacked generalization uses the destination dataset... to determine the coefficients... The partition of the learning set... is crucial.\" [1]\nAs established in the foundational literature on stacked generalization, proper partitioning is required to avoid overfitting. The huge discrepancy between base model performance and meta-learner performance in this paper is a hallmark of evaluating the stacker on its training data.\n\nReferences:\n[1] Wolpert, D. H. (1992). Stacked generalization. Neural networks, 5(2), 241-259. https://doi.org/10.1016/S0893-6080(92)00049-7", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|46|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb46", "comment": "The abstract and conclusion claim that the polyBERT approach \"preserves accuracy\" compared to the state-of-the-art Polymer Genome (PG) fingerprints, but the results demonstrate a significant degradation in performance for several key properties.\n\n\"The present approach outstrips the best presently available concepts... while preserving accuracy\" (Abstract)\nThis claim is contradicted by the authors' own data in Table S1. \"Preserving accuracy\" implies parity or negligible difference, but the results show substantial drops for multiple properties.\n\"cp ... R2 PB 0.61±0.11 ... R2 PG 0.76±0.10\" (Table S1)\nFor heat capacity (cp), the R2 drops from 0.76 (PG) to 0.61 (polyBERT). This is a significant loss in predictive power, not a preservation of accuracy.\n\"Oi ... R2 PB 0.57±0.16 ... R2 PG 0.61±0.16\" (Table S1)\nFor limiting oxygen index (Oi), polyBERT performs worse than PG.\n\"σb ... R2 PB 0.76±0.05 ... R2 PG 0.79±0.04\" (Table S1)\nFor tensile strength at break, polyBERT is again inferior. The consistent pattern of PG outperforming polyBERT in the cross-validation results undermines the central claim of the paper.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|46|Gemini|5", "source": "prb", "split": "test", "paper_id": "prb46", "comment": "The reliance on a training dataset of 100 million \"hypothetical\" polymers generated by fragment recombination raises concerns about the chemical validity and synthesizability of the structures, which may bias the model.\n\n\"The hypothetical PSMILES strings are chemically valid polymers but, mostly, have never been synthesized before.\" (Results)\nWhile the strings may be valid in terms of SMILES syntax (valence rules), \"hypothetical\" combinations of fragments often result in unstable or synthetically inaccessible structures. Training a foundation model primarily on such data (100M hypothetical vs 13k known) risks encoding unrealistic chemical features, potentially leading to \"hallucinations\" or poor performance on real-world, complex polymer chemistries that deviate from the combinatorial logic of the training set.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|46|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb46", "comment": "The source of the 13766 polymers synthesized so far should be listed.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|46|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb46", "comment": "The number and distribution of tokens identified by the SentencePiece tokenizer should be reported with a more comprehensive set of their examples.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|46|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb46", "comment": "Compared to homopolymers, the data set of copolymers is quite small. Therefore, the representation ability for copolymers may be inferior to that of homopolymers. I request that you separately compare the prediction performance of homopolymers and copolymers in benchmarking the property prediction tasks.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|46|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb46", "comment": "I understood that a copolymer is given into the model simply by concatenating the SMILES strings of its monomers with periods. If this understanding is correct, the model will not be able to distinguish random, alternating copolymers, etc. This should be remarked as a limitation.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|46|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb46", "comment": "It is obvious that the computation times of polyBERT and PG are linear with respect to the number of polymers, since the computation of multiple polymers is completely independent. In the last paragraph on page 12, there is no need to emphasize that it is linear.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|46|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb46", "comment": "In the manuscript, it is stated that the accuracy of the property prediction was evaluated on the validation set, but is this a mistake for the test set? The validation set should never be used to evaluate the prediction performance of a model.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|46|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb46", "comment": "The difference between ordinary fingerprints such as PG and the polyBERT representations should be investigated in more detail. In the property prediction benchmark, the reported prediction accuracy of the two is almost equal. One question here is; does using a descriptor that concatenates PG and polyBERT fingerprints improve prediction accuracy? If there are no intrinsic differences between the two, the prediction accuracy would not be different from models with PG and polyBERT fingerprints alone. The difference between the two can also be examined as follows: For a set of test polymers, their similarity matrix can be computed with the PG or polyBERT features, respectively. These two matrices can be compared visually (e.g. using heatmaps) or quantitatively to identify a subset of polymers differently represented by the two descriptors.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|46|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb46", "comment": "I am curious about the generation of the 100 million hypothetical PSMILES strings to train the polyBERT model. Is 100 million just an arbitrarily big number necessary for training, or can this purpose be achieved with a smaller dataset?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|46|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb46", "comment": "In table 1, it appears there is a heavy mismatch between datasets for different properties, as well as some mixing and matching going on in terms of experimental and DFT datasets. From Figure 5, it appears that every property is predicted highly accurately. Please shed some light on this- how much does the size and source of data affect the actual property predictions?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|46|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb46", "comment": "There are a couple of spelling errors, such as the word \"originallydro\" on page 18. Please check.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|46|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb46", "comment": "Compared with polymer Genome (PG), polyBERT shows rival or slightly worse prediction accuracy in most benchmarks. Thus, the major benefit of polyBERT compared with polymer Genome (PG) is the prediction speed. As shown in Figure 4, when dealing with 10^4 PSMILES, PG takes 4-5 hours while polyBERT takes only few seconds when using GPU, which is a huge improvement. However, the computational time using PG to deal with 10^4 PSMILES is not totally unacceptable. The authors are suggested to comment on the magnitude of polymer data for virtual screening in practice to further validate the benefits of polyBERT. Also, in terms of the computational time, what is the pretraining plus finetuning time of polyBERT when comparing to PG. I suggest the authors include training time for fair comparison of the computation time.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|46|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb46", "comment": "In page 5, the authors mention “We also note that unlike Transformers graph neural networks are usually trained end-to-end, i.e., their latent space representations (fingerprints) are learned under supervision with polymer properties.” It is true that pretrained Transformer has been a widely used scheme in machine learning. However, there are also many works investigating pretraining graph neural networks, e.g., https://openreview.net/forum?id=HJlWWJSFDH, https://www.nature.com/articles/s42256-022-00447-x, https://www.nature.com/articles/s42256-021-00438-4, https://proceedings.neurips.cc/paper/2021/hash/85267d349a5e647ff0a9edcb5ffd1e02-Abstract.html. I suggest the authors include necessary discussions on GNN pretraining as well.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|46|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb46", "comment": "polyBERT is built upon DeBERTa, a variant of Transformer-based model. I suggest the authors provide more discussion about why DeBERTa, instead of other BERT-like models, is preferred for polymers in this work.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|46|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb46", "comment": "Using BRICS decomposition can generate hypothetical PSMILES. However, it can also generate unrealistic polymers. Will this affect the performance of the model?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|46|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb46", "comment": "This work introduces PSMILES canonicalization, which helps get clean polymer representations. Can un-canonicalized PSMILES used for augmentation of training data?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|46|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb46", "comment": "PSMILES used in this work is based on SMILES with stars to indicate repeat units. Have the authors consider using existing sequence representations like BigSMILES (https://pubs.acs.org/doi/10.1021/acscentsci.9b00476)?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|46|Human_3|7", "source": "prb", "split": "test", "paper_id": "prb46", "comment": "In multitask learning shown in FigureS2, selector vectors are determined based on properties, e.g., electrical, mechanical, permeability, etc. Will multitask learning among different properties help? Did the authors have data analysis on the correlation different polymer properties?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|46|Human_3|10", "source": "prb", "split": "test", "paper_id": "prb46", "comment": "Page 8 writes “The validation F1-score is > 99.” I suppose this is a typo and the authors mean that F1-score is > 0.99.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|47|Claude|1", "source": "prb", "split": "test", "paper_id": "prb47", "comment": "The paper claims these artificial fingerprints are \"unclonable unique objects\" but fails to provide rigorous security analysis against potential cloning attacks using advanced nanolithography techniques, while acknowledging this vulnerability only briefly in the Discussion section.\n\n\"Here, we report on artificial fingerprints that can be directly engraved on a wide range of substrates through self-assembled block-copolymer templating for secure authentication and identification. We show that engraved nanopatterns are unclonable unique objects...\"\nThe paper makes strong claims about unclonability in the abstract, positioning this as a key contribution. However, the security analysis to support this claim is not rigorous. For a PUF system claiming to be secure, the paper should provide threat modeling, analyze potential attack vectors, and quantify the difficulty or cost of cloning attempts. The standard for PUF security analysis typically includes modeling attacks, side-channel attacks, and physical cloning attempts, none of which are addressed systematically.\n\"Indeed, since it cannot be excluded a priori that a nanopattern can be cloned by using advanced and expensive lithographic tools with resolution < 10 nm (even if this is unlikely), line-edge roughness, line-width roughness, and the 3D morphology of systems are unlikely to be reproducible.\"\nThis admission in the Discussion section directly contradicts the \"unclonable\" claims made elsewhere. Modern EUV lithography and multi-beam electron beam lithography can achieve sub-10 nm resolution. The paper's dismissal of this threat as \"unlikely\" without quantitative analysis is insufficient. According to semiconductor industry roadmaps, EUV systems can achieve 7 nm features, and e-beam lithography routinely achieves sub-5 nm resolution for research applications. The paper does not provide cost-benefit analysis of potential cloning attempts.\n\"Physical Unclonable Functions (PUFs) include several families: Arbiter PUFs...yielding many challenge–response pairs (CRPs) but making them vulnerable to modeling and side-channel attacks when CRPs are exposed\" [[1]](#citation-1)\nThe PUF security literature extensively documents various attack vectors against PUF systems, including machine learning-based modeling attacks. The reviewed paper does not address whether its image-based nanopattern PUF is vulnerable to similar attacks where an adversary could attempt to learn and replicate the statistical properties of the patterns rather than cloning them directly.\n\nReferences:\n[1] InterPUF: Distributed Authentication via Physically Unclonable Functions. arXiv:2601.11368v1 (2025). https://arxiv.org/html/2601.11368v1", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|47|Claude|2", "source": "prb", "split": "test", "paper_id": "prb47", "comment": "The entropy equation presented in the Methods section is mathematically incorrect, deviating from the standard binary entropy formula, which affects the reproducibility and methodological clarity of the paper.\n\n\"The unit entropy of the i-th binarized code matrix have been evaluated through the Eq. 1: $$E_{i}= -\\left[p_{i}{\\text{log}}_{2}{p}_{i}+(1-{p}_{i}){\\text{log}}_{2}{p}_{i}(1-{p}_{i})\\right]$$\"\nThe formula as written is mathematically incorrect. The standard Shannon binary entropy formula is H(p) = -[p·log₂(p) + (1-p)·log₂(1-p)]. The paper's second term shows \"(1-p_i)·log₂(p_i)·(1-p_i)\" instead of \"(1-p_i)·log₂(1-p_i)\". When evaluated at p=0.5 (the optimal bit uniformity), the correct formula yields 1.0, but the paper's formula yields 0.75. Since the paper reports entropy values \"approaching the ideal value of 1 when bit uniformity is close to 0.5,\" the actual calculations likely used the correct formula, making this a transcription error that nonetheless affects reproducibility.\n\"This is because bit uniformity is beneficial to achieve the maximum randomness, as testified by the maximum pattern entropy approaching the ideal value of 1 when bit uniformity is close to 0.5\"\nThe paper correctly identifies that entropy should approach 1 when bit uniformity is 0.5, which would be impossible using the formula as written in the paper. This inconsistency between the stated formula and the described results creates confusion about the actual methodology used and makes it difficult for other researchers to reproduce the entropy calculations.\n\"Uniformity: It is the probability that the 0s and 1s are uniformly distributed in PUF's response.\" [[2]](#citation-2)\nThe standard PUF literature uses well-established formulas for entropy and uniformity metrics. The error in the paper's entropy formula deviates from these established standards, making it difficult for researchers in the PUF field to validate or compare results.\n\nReferences:\n[2] Securing IoT Networks Using Machine Learning-Resistant Physical Unclonable Functions. MDPI Network 6(1), 6 (2025). https://www.mdpi.com/2673-8732/6/1/6", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|47|Claude|3", "source": "prb", "split": "test", "paper_id": "prb47", "comment": "The paper's astronomical encoding capacity claims assume perfect independence between binary code matrix pixels, ignoring the spatial correlations inherent in block copolymer self-assembly, which leads to significant overestimation of the effective encoding capacity.\n\n\"In this context, the encoding capacity of the system c^p, defined as the number of possible responses exhibited by a random pattern where c is the number of responses for each pixel while p is the image area in pixels...an encoding capacity larger than the number of atoms in the known universe is achievable by considering an image area larger than 12 µm²\"\nThe encoding capacity formula c^p (where c=2 for binary) assumes that each pixel is statistically independent of every other pixel. However, block copolymer self-assembly produces patterns with significant spatial correlations, as the paper itself acknowledges through the correlation length measurement. The paper reports a correlation length of ξ = 207 ± 18 nm, which means that pixels within this distance are correlated, not independent. This spatial correlation fundamentally reduces the effective degrees of freedom and thus the true encoding capacity.\n\"It is noteworthy that, a bit uniformity (and fractional HD) of 0.5 can be observed when the pixel size approximately coincides with the correlation length of BCP patterns (ξ = 207 ± 18 nm, details in Methods).\"\nThe paper's own data shows that the pixel size must match the correlation length to achieve optimal entropy. This implicitly acknowledges that pixels smaller than the correlation length would not be independent. However, the encoding capacity calculation uses the total number of pixels without accounting for this correlation, leading to overestimation. A more accurate calculation would need to use the effective number of independent bits, which is bounded by the ratio of image area to correlation area.\n\"The bit uniformity (pᵢ) of the i-th binarized code matrix...calculated through the equation: p_{i}=\\frac{1}{n}\\sum_{k=1}^{n}{R}_{i,k}...A value of 1 means that all responses Rᵢ,ₖ of the i-th pattern are logic-1.\"\nThe bit uniformity is reported as 0.52 ± 0.06, not exactly 0.5. This deviation from ideal uniformity further reduces the actual entropy per pixel from the theoretical maximum of 1 bit. Combined with spatial correlations, the true encoding capacity would be substantially lower than the claimed astronomical values.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|47|Claude|4", "source": "prb", "split": "test", "paper_id": "prb47", "comment": "The thermal and aging stability tests are limited in scope (6 months aging, 200°C/30 minutes thermal), which is insufficient to support the paper's claims about robustness for real-world commercial and industrial applications.\n\n\"Aging stability was evaluated by collection of the SEM images of the same set of devices after 6 months from its fabrication, by storing devices at normal ambient conditions.\"\nA 6-month aging test at ambient conditions provides limited information about long-term stability. Industrial reliability standards typically require accelerated life testing that simulates years of use, including temperature cycling, humidity exposure, and mechanical stress. For applications mentioned in the paper such as chip authentication and supply chain security, devices may need to remain functional for 10+ years under varying conditions. The paper does not provide data to support such long-term reliability.\n\"The thermal stability of PUF devices was tested by subjecting the samples to a heat treatment by the rapid thermal annealing at 200°C for 30 minutes.\"\nWhile 200°C for 30 minutes demonstrates some thermal tolerance, this single test condition does not comprehensively address thermal stability. Real-world applications involve repeated thermal cycling, varying temperature ranges (including cryogenic for some applications), and combined temperature-humidity stress. Standard reliability testing protocols like JEDEC standards for electronics require temperature cycling between extremes (e.g., -55°C to +125°C) for hundreds or thousands of cycles.\n\"The BCH-coded fuzzy extractor tolerates up to 15% bit error rate (BER), ensuring reliable key regeneration across temperature variations (−20 °C to 70 °C), voltage fluctuations, and device aging effects.\" [[3]](#citation-3)\nThe PUF reliability literature recognizes that environmental factors cause bit errors over time, and sophisticated error correction is needed to maintain reliability. The reviewed paper does not report bit error rates under different environmental conditions or demonstrate that the nanopatterns maintain stability within acceptable error bounds over extended periods.\n\nReferences:\n[3] A Lightweight Authentication and Key Distribution Protocol for Extended Reality Systems. PMC (2025). https://pmc.ncbi.nlm.nih.gov/articles/PMC12788305/", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|47|Claude|5", "source": "prb", "split": "test", "paper_id": "prb47", "comment": "The requirement for scanning electron microscopy (SEM) to read the PUF response represents a fundamental practical limitation that severely constrains deployment in real-world authentication scenarios, despite the paper's attempt to frame this as a security feature.\n\n\"While on one hand the requirement of an electron microscope to challenge the PUF with a scanning focused electron beam can represent an obstacle (despite recent advances in low-cost and portable SEM equipment), on the other hand the requirement of a specialized equipment can further enhance the security of the authentication/identification process in a multiple-level security scenario.\"\nThe paper acknowledges the SEM requirement as an \"obstacle\" but attempts to reframe it as a security feature. However, even \"low-cost\" SEM equipment costs tens of thousands to hundreds of thousands of dollars, requires vacuum operation, trained operators, and is not portable for field use. This fundamentally limits the applicability compared to other PUF technologies that use optical readout methods accessible with smartphone cameras or inexpensive readers.\n\"Note that the unique response of the PUF pattern can be probed also through other imaging techniques, such as atomic probe microscopy (AFM).\"\nThe paper mentions AFM as an alternative, but AFM is even slower and more equipment-intensive than SEM. Neither technique enables the rapid, on-site authentication that would be needed for supply chain verification or consumer product authentication. Previous work on block copolymer PUFs has explored optical readout methods that would be more practical for widespread deployment.\n\"Optical physical unclonable functions based on Förster resonant energy transfer in multi-color quantum dots...Communications Materials (2025)\" [[4]](#citation-4)\nRecent developments in optical PUF technologies demonstrate that achieving practical readout with simpler equipment is an active area of research. The reviewed paper's reliance on electron microscopy places it at a significant practical disadvantage compared to PUF approaches that can be read using simpler optical methods, limiting the real-world impact of the work despite its scientific contributions.\n\nReferences:\n[4] Kim, J.H. et al. Nanoscale physical unclonable function labels based on block copolymer self-assembly. Nature Electronics 5, 433–442 (2022). https://www.nature.com/articles/s41928-022-00788-w", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|47|GPT|1", "source": "prb", "split": "test", "paper_id": "prb47", "comment": "This paper makes inadequately supported claims of “unclonability” and of meeting “main requirements of PUFs” without specifying an adversary model, attack surface, or a security notion tied to realistic cloning/modeling attacks for the proposed SEM-readable nano-fingerprint component.\n\n“We show that engraved nanopatterns are unclonable unique objects that endow high encoding capacity density while satisfying main requirements of PUFs…”\nThis sentence asserts a strong security property (“unclonable”) and broad compliance with PUF requirements, which in hardware-security practice requires an explicit threat model and demonstrated resistance against relevant attacker capabilities. However, the manuscript’s experiments primarily quantify uniqueness-like behavior (e.g., inter- vs intra-Hamming distance separation) under benign acquisition conditions, which is not the same as adversarial unclonability. Without defining what “cloning” means here (physical replication of topography, digital replay of images, fabrication of statistically matching patterns, etc.), the conclusion is not verifiable. In addition, the reader cannot assess whether the evaluated protocol prevents an attacker from producing a counterfeit that passes the same matching pipeline. This gap directly affects the validity of the central security claim.\n“Indeed, since it cannot be excluded a priori that a nanopattern can be cloned by using advanced and expensive lithographic tools with resolution < 10 nm (even if this is unlikely)…”.\nThis admission materially weakens the unconditional “unclonable” framing because it concedes that physical replication cannot be ruled out even in principle, while providing no quantitative or procedural analysis of that risk. In anti-counterfeiting/PUF work, it is common to either (i) scope the adversary and argue infeasibility under that scope, or (ii) provide empirical evidence that known replication routes fail. Here, the paper instead relies on an intuition (“unlikely”) without describing required tool access, process tolerances, or how a clone would be detected by the proposed verification algorithm. That makes the “unclonable” conclusion dependent on unstated assumptions about attacker resources and process control. As a result, the main security conclusion is not robust.\n“These artificial fingerprints can be considered as PUF where the nanopattern represents the unique response r when the surface is scanned with a focused beam of electrons representing the input challenge c.”\nThis definition effectively collapses the “challenge” to an imaging procedure, which is close to a fixed-challenge setting unless the authors explicitly demonstrate a large, controlled challenge space and show that responses are secure under chosen-challenge access. In such settings, security is typically determined by what an attacker can learn or reproduce after observing responses (e.g., collecting micrographs, learning the matching thresholds, or fabricating a copy). The manuscript does not describe an attack game (e.g., chosen-challenge cloning, replay, or measurement-and-recreate) that would connect the PUF framing to security outcomes. The statement therefore does not establish that the construction behaves as a secure PUF in the sense used in hardware-security literature. This undermines the paper’s validity claims about PUF security, beyond uniqueness.\n“Building on the theory of physical functions, we rigorously define robustness, unclonability, and unpredictability for chemical functions … and specify security games that capture the adversary’s power and the security goals.” [[3]](#ref3)\nThis excerpt illustrates a common practice in physical/chemical-function security: security properties like unclonability are tied to explicit adversary capabilities and success conditions. Even though this reference addresses chemical functions, it is explicitly “building on the theory of physical functions” and shows the level of formalization expected when making unclonability claims. By contrast, the reviewed paper does not define attacker access (e.g., number of measurements, ability to purchase devices, imaging resolution, fabrication capabilities) or the success criterion (passing which verifier, under which noise model). The discrepancy matters because “unclonable” is not an observational property; it is a property under attack. Without comparable adversary-scoped definitions, the reviewed paper’s “unclonable” conclusion is not established.\n“Arbiter PUFs … yield many challenge–response pairs (CRPs) but making them vulnerable to modeling and side-channel attacks when CRPs are exposed …” [[4]](#ref4)\nThis passage highlights that PUF security depends critically on how challenge–response information is exposed and used, not just on uniqueness metrics. The reviewed paper’s protocol relies on image acquisition and matching, which necessarily exposes response information (binarized patterns and similarity scores) to whoever performs verification. Yet the manuscript does not analyze whether exposure of such information enables replay/modeling strategies, nor does it discuss limiting information leakage (e.g., through on-device hashing, controlled interfaces, or secure enrollment/verification protocols). This omission is significant because many PUF deployments fail when the interface leaks enough structure for prediction or counterfeiting. Therefore, the paper’s security conclusions are incomplete relative to established PUF threat considerations.\n\nReferences:\n[3] [Walter et al., “A Security Framework for Chemical Functions” (arXiv:2601.14019)](https://arxiv.org/html/2601.14019v1)\n[4] [Tashdid et al., “InterPUF: Distributed Authentication via Physically Unclonnable Functions…” (arXiv:2601.11368)](https://arxiv.org/html/2601.11368v1)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|47|GPT|2", "source": "prb", "split": "test", "paper_id": "prb47", "comment": "This paper over-interprets bit-uniformity and a per-pattern “unit entropy” proxy as evidence of cryptographically meaningful entropy and extreme “encoding capacity,” without analyzing spatial/bit dependencies or min-entropy for the binary-code-matrix encoding component.\n\n“This is because bit uniformity is beneficial to achieve the maximum randomness, … as testified by the maximum pattern entropy approaching the ideal value of 1 when bit uniformity is close to 0.5…”\nThe quoted reasoning conflates balance (≈50/50 zeros and ones) with unpredictability and usable entropy for security purposes. A balanced bitstream can still be highly predictable if there are spatial correlations, deterministic structures, or dependencies between bits (which are plausible in self-assembled lamellae even after binarization). The manuscript does not report any independence tests, correlation analyses on the resulting bit matrices, or a conservative entropy metric appropriate for adversaries. As a result, “entropy approaching 1” here functions as a descriptive statistic rather than a validated security measure. The paper’s conclusion that the encoding has “high entropy” is therefore not supported at the level implied.\n“Interestingly, an encoding capacity of the same order of magnitude of the world population can be achieved … while an encoding capacity larger than the number of atoms in the known universe is achievable …”.\nThese claims are extraordinary and hinge on treating each pixel/bit as an independent degree of freedom, which is not demonstrated in the paper. In practical PUF/biometric-style systems, the effective number of distinguishable identities depends on both entropy and reliability under noise, including how often re-measurements flip bits and how much error correction is needed. The manuscript discusses misalignment sensitivity and later switches to a vision-based matching protocol, suggesting that the raw code-matrix representation is fragile to real-world transforms. That fragility typically reduces effective capacity because many nominal codes may not be reliably reproducible or separable under deployment conditions. Without quantifying effective min-entropy and reproducible key space under realistic noise and correlation, the “atoms in the universe” conclusion is not reliable.\n“It is noteworthy that, a bit uniformity (and fractional HD) of 0.5 can be observed when the pixel size approximately coincides with the correlation length of BCP patterns (ξ = 207 ± 18 nm…)”.\nInvoking a correlation length underscores that the underlying physical field is spatially correlated, which is exactly the condition under which per-pixel independence assumptions are suspect. Choosing pixel size near a correlation length may reduce some redundancy, but it does not establish that adjacent pixels are independent or that higher-order dependencies are negligible. The paper does not provide any quantitative justification that the resulting binary matrices satisfy assumptions needed for entropy/capacity extrapolations (e.g., independence, stationarity, or a validated stochastic model). Without such validation, the link from “correlation length” to “ideal entropy” is an unsupported leap. This directly affects the validity of the paper’s capacity and entropy conclusions.\n“This Recommendation uses a very conservative measure known as min-entropy, which measures the effectiveness of the strategy of guessing the most likely output of the entropy source.” [[1]](#ref1)\nThis statement highlights that security-relevant randomness should be evaluated using conservative measures tied to an attacker’s best-guess strategy, not only balance-based metrics. The reviewed paper’s “unit entropy” computation is derived from bit-uniformity and does not bound an attacker’s guessing success when bits are dependent or when some patterns are more likely than others. Moreover, the paper does not estimate min-entropy or provide bounds on the most likely codes under the fabrication process and extraction pipeline. Because the manuscript frames the codes as security-bearing (“high entropy” and extreme “encoding capacity”), the absence of a conservative entropy analysis is a significant methodological gap. This undermines the strength of the stated conclusions.\n“The IID track shall be used only when … the IID assumption is verified (i.e., there is no evidence that the data is not IID).” [[1]](#ref1)\nThis excerpt emphasizes that independence claims require explicit statistical verification, even in formal randomness evaluation settings. The reviewed paper does not test IID-like properties of the generated bit matrices, despite using a physical process with known spatial structure and correlation. Without testing for dependence, it is not justified to interpret a high per-bit Shannon-style entropy proxy as evidence of near-ideal randomness. This matters because dependence can drastically reduce effective key space and increase predictability. Therefore, the paper’s entropy/capacity interpretation is methodologically incomplete.\n\nReferences:\n[1] [NIST Special Publication 800-90B: Recommendation for the Entropy Sources Used for Random Bit Generation (Jan 2018)](https://nvlpubs.nist.gov/nistpubs/SpecialPublications/NIST.SP.800-90B.pdf)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|47|GPT|3", "source": "prb", "split": "test", "paper_id": "prb47", "comment": "This paper’s authentication/identification experiment and thresholding for the computer-vision matching component does not provide statistically robust estimates of error rates (e.g., FAR/FRR as functions of threshold, uncertainty bounds, and evaluation on an independent test protocol), yet draws strong reliability conclusions.\n\n“A clear separation … (mean values and std. dev. of inter and intra-HD distributions are 0.14 ± 0.01 and 0.500 ± 0.003, respectively). Here, a HD-based decision threshold of 0.45 can be identified…”.\nThe paper selects a single operating threshold but does not report a full operating-characteristic curve that would show how false accept and false reject trade off across thresholds. Reporting only mean and standard deviation of two distributions is insufficient to characterize tail behavior, which determines false positives/negatives in biometric-like verification systems. Moreover, the manuscript does not state whether the threshold was chosen using the same comparisons used to report performance, which risks optimistic bias if not done on a held-out validation set. The cited ± values also lack a clear definition of uncertainty (e.g., SD across what unit, SE, or confidence intervals). Without these details, the robustness of the conclusion about a safe decision threshold is unclear.\n“In all these cases, successful authentication/identification of all PUF patterns without any false positive or false negative have been achieved by exploiting the decision threshold of 0.45…”\nA “zero-error” outcome on a finite evaluation does not, by itself, establish that the error rate is negligible; it primarily reflects that no errors were observed in the particular sample size and test protocol. For authentication systems, the practical question is the achievable FAR/FRR under expected deployment variation, and the uncertainty around those estimates given limited sample sizes. The manuscript does not provide confidence intervals or upper bounds for FAR/FRR implied by “no errors,” nor does it show how performance changes under more challenging impostor sets or acquisition conditions. In addition, the stated threshold is very close to the inter-HD mean (~0.5), suggesting that modest shifts in distribution tails could cause errors, which should be quantified. Therefore, the conclusion that the protocol yields robust real-world authentication is not statistically substantiated.\n“Then we select a few points providing the best matches (we tested between 10–15, not significantly affecting the results)…”\nThis statement indicates that key hyperparameters of the matching pipeline (number of matches retained) were tuned or explored, but the paper does not report a principled selection procedure or sensitivity analysis across broader ranges and conditions. In computer-vision matching, small changes in feature selection, RANSAC thresholds, and preprocessing can shift the overlap quality distribution, particularly for near-miss impostors. Simply asserting “not significantly affecting the results” without presenting quantitative ablations (and without defining what “significant” means) is insufficient when the downstream claim is “no false positives or false negatives.” This is especially important because the decision threshold is a single scalar; any pipeline change that shifts intra/inter distributions can change errors. The lack of systematic uncertainty quantification weakens confidence in the reported robustness.\n“Receiver operating characteristic (ROC) curve analysis is widely used in evaluating the effectiveness of a diagnostic test/biomarker or classifier score.” [[6]](#ref6)\nThis sentence summarizes common practice for evaluating thresholded decision systems: characterize performance across thresholds rather than relying on a single chosen operating point. The reviewed paper’s matching protocol is directly analogous to a binary classifier (accept/reject based on HD), yet it does not provide ROC-like reporting (or equivalent FAR/FRR curves) for the main experiments. While the paper shows separation in means, it does not quantify how separation translates into operational error trade-offs under varying conditions. ROC-style evaluation would also naturally support reporting uncertainty (e.g., confidence intervals on AUC or on operating points), which is absent here. Thus, by standard evaluation norms for verification systems, the statistical evidence is incomplete.\n\nReferences:\n[6] [Bantis et al., “Statistical Inference for Box-Cox based Receiver Operating Characteristic Curves” (PMC, 2024)](https://pmc.ncbi.nlm.nih.gov/articles/PMC11957834/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|47|GPT|4", "source": "prb", "split": "test", "paper_id": "prb47", "comment": "This paper’s central pipeline (SEM-image preprocessing → fingerprint enhancement → defect extraction/encoding and matching) is not fully reproducible from the provided code/materials because essential steps rely on external tools and modified scripts that are not included or precisely specified, and the provided matching script has failure modes that can prevent rerunning analyses on new data.\n\n“The fingerprint enhancement algorithm … was adapted from the algorithm described in ref. 37 by exploiting the fingerprint_enhancement python library. Parameters of the enhance_Fingerprint function were adapted…”\nThis description omits the concrete parameter settings and versioning needed to reproduce the binarization step, which is explicitly positioned as crucial for reducing artifacts and enabling user-independent extraction. Because the downstream metrics (defect maps, bit uniformity/entropy, matching HD) depend on the binarized output, small implementation or parameter differences can materially change results. The paper states that parameters were “adapted” based on pitch and resolution, but it does not provide the adaptation rule, the exact parameter values, or reference configurations for the reported experiments. As a result, an independent researcher cannot reliably reproduce the exact binarized patterns used in the reported analyses. This is a major reproducibility issue because binarization is the foundation of both the code-matrix and matching pipelines.\n“Spatial coordinates, types, and density of topological defects … was performed through the automated defect analysis tool ADAblock … modified to be integrated into an automated analysis process…”\nThe paper acknowledges that ADAblock was modified, which means reproduction requires access to the specific modified version and a description of the modifications. However, the manuscript does not include those modifications or a patch/diff, nor does it provide a precise commit hash or archival reference for the modified tool. In workflows where defect detection defines the binary code matrix, undocumented modifications can change defect counts, types, and locations, directly affecting reported entropy/HD statistics. Stating that a tool was “modified” is insufficient for reproducibility without releasing the modified code or describing changes in detail. This weakens confidence that the reported quantitative results can be independently verified.\n“The script 'sem_image_automated_preprocessing_for_ADAblok.py' to analyze and binarize SEM images is provided at the following GitHub repository: https://github.com/ChiaraMagosso/BlockMetrology. We highly recommend to follow the readme instruction … and uncomment the line of code where indicated…”\nThis shifts a core part of the pipeline (preprocessing and binarization for ADAblock) to an external repository and implies manual code-edit steps (“uncomment the line”) to obtain correct behavior. Without pinning a specific version of that external repository and documenting exactly which lines must be toggled, the pipeline is not reproducible in the sense expected for computational sections of a research paper. It also introduces hidden degrees of freedom: different users may enable different modes or run slightly different preprocessing paths, producing different binarizations and defect coordinates. Because the paper’s main claims depend on these outputs, this external/manual dependency materially impacts reproducibility. This is not a minor “documentation” issue; it is a dependency gap for core methodology.\n“The modified script ADAblock.ijm can be found at … To set up ADAblock, follow …” [[5]](#ref5)\nThis evidence corroborates that the workflow depends on a nontrivial toolchain (ImageJ macros and setup instructions) beyond the code shipped with the paper’s repository snapshot. Such multi-tool pipelines can be reproducible, but only if the paper pins exact versions, provides a run script, and archives all modified components. Here, the reviewed paper does not provide a single end-to-end entry point that recreates the reported figures/metrics from raw SEM images. The reliance on external setup instructions also increases the chance of environment-dependent behavior, which is especially relevant for image processing. This compounds the reproducibility problem already implied by “modified” tooling in the paper.\n```python\nif len(good)>MIN_MATCH_COUNT:\n    ...\n    matchesMask = mask.ravel().tolist()\n    ...\nelse:\n    print( \"Not enough matches are found - {}/{}\".format(len(good), MIN_MATCH_COUNT) )\n    warped_img1 = img1\n\n...\n\ndraw_params = dict(\n    matchesThickness = 8,\n    matchesMask = matchesMask, \n    flags = cv.DRAW_MATCHES_FLAGS_DRAW_RICH_KEYPOINTS)\n```\nAs written, this code can fail at runtime because `matchesMask` is only defined in the success branch, but is used unconditionally later when drawing matches. This is a substantive reproducibility risk: the matching procedure will crash exactly in difficult cases (insufficient matches), which are common in realistic or lower-quality acquisitions and in impostor comparisons. A paper that claims robust authentication across users/equipment should provide matching code that gracefully handles failure cases (e.g., define `matchesMask=None` and skip drawing, or handle empty descriptors). If the script fails on some pairs, it also biases any reported statistics toward easy cases unless carefully audited. Therefore, the provided code does not reliably support independent reruns of the paper’s matching evaluation.\n\nReferences:\n[5] [ChiaraMagosso/BlockMetrology (GitHub repository)](https://github.com/ChiaraMagosso/BlockMetrology)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|47|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb47", "comment": "The proposed PUF system relies on Scanning Electron Microscopy (SEM) for readout, which severely limits its practical applicability for \"supply chain\" and \"mass production\" scenarios, contradicting the paper's motivation.\n\n\"Counterfeiting represents a growing problem for society that has not only enormous economic implications, from manufacturing of goods to specialized technologies\"\nThe authors motivate their work by addressing the broad problem of counterfeiting in the manufacturing and supply chain sectors, implying that their solution is applicable to these fields.\n\"The micrographs of artificial fingerprints were acquired by FEI Inspect-F field emission gun scanning electron microscope (FEG-SEM)\"\nThe readout method requires a Scanning Electron Microscope (SEM), which is a large, expensive, and slow instrument often requiring vacuum conditions and sample preparation (e.g., coating). This is incompatible with the high-throughput, low-cost requirements of standard supply chain verification.\n\"While on one hand the requirement of an electron microscope to challenge the PUF with a scanning focused electron beam can represent an obstacle... on the other hand the requirement of a specialized equipment can further enhance the security\"\nThe authors acknowledge the limitation but attempt to frame it as a security feature. However, this \"obstacle\" effectively precludes the use of the technology for its stated purpose (protecting goods in the supply chain) where inspectors or consumers need easy verification.\n\"Nanoscale physical unclonable function labels based on block copolymer self-assembly\" [1]\nOther works in the field, such as Kim et al. [1], have successfully demonstrated BCP-based PUFs using optical readout methods (e.g., Raman spectroscopy or birefringence), which are far more practical for real-world deployment than SEM.\n\nReferences:\n[1] J. H. Kim et al., \"Nanoscale physical unclonable function labels based on block copolymer self-assembly,\" Nature Electronics, vol. 5, pp. 433–442, 2022. https://www.nature.com/articles/s41928-022-00788-w", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|47|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb47", "comment": "The reported Intra-Hamming Distance (Intra-HD) of 0.14 is excessively high for a reliable PUF, and the paper fails to address the necessary error correction to generate stable cryptographic keys.\n\n\"mean values... of intra... HD distributions are 0.14 ± 0.01\"\nAn Intra-HD of 0.14 means that 14% of the bits (or pixels) change between repeated measurements of the same PUF. For a stable cryptographic key, the Bit Error Rate (BER) typically needs to be close to 0 (or correctable to 0). A 14% raw error rate is very high and would require heavy Error Correction Codes (ECC) to be usable as a key, which are not discussed.\n\"Even small translations, rotations and/or deformations of the end user image can cause incorrect authentication/identification due to a different conversion of the fingerprint pattern to the binary code matrix. Indeed, these transformations can cause bit flips in the related binary code matrix\"\nThe authors admit that the \"binary code matrix\" approach is unstable due to alignment issues. While they propose an image-matching alternative for authentication, this does not solve the problem of generating stable \"cryptographic codes\" as claimed.\n\"Physical unclonable functions and applications: A tutorial\" [2]\nAs established in the PUF literature [2], reliable key generation requires low intra-device variation (typically <5-10% raw BER) to be correctable by standard fuzzy extractors. The reported 14% variation is significantly higher than the norm for robust PUFs.\n\nReferences:\n[2] C. Herder, M.-D. Yu, F. Koushanfar, and S. Devadas, \"Physical unclonable functions and applications: A tutorial,\" Proceedings of the IEEE, vol. 102, no. 8, pp. 1126–1141, 2014. https://ieeexplore.ieee.org/document/6823677", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|47|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb47", "comment": "The paper heavily employs the analogy of human fingerprint \"minutiae\" (topological defects) to describe the system, but the robust authentication algorithm relies on standard texture matching (SIFT and pixel-wise XOR) rather than minutiae-based matching.\n\n\"Notably, these patterns are characterized by the presence of spatially distributed local features (defect points) closely resembling minutiae points of human fingerprints.\"\nThe paper spends significant effort defining and analyzing these topological defects (terminations, junctions) in Figures 1, 2, and 3, establishing the \"fingerprint\" analogy.\n\"matching key points... are computed through a Scale-Invariant Feature Transform (SIFT)... use those as a guide to build a homography... quantification... is performed by calculating the fractional HD\"\nThe actual robust matching method described in Figure 4 uses SIFT, which detects local contrast extrema (blobs/corners), not the topological minutiae defined earlier. The matching is then done by pixel-wise XOR (Hamming Distance) of the aligned images.\n```python\nkp1, des1 = sift.detectAndCompute(img1,None)\nkp2, des2 = sift.detectAndCompute(img2,None)\n```\nThe code confirms that standard SIFT keypoints are used for alignment, effectively discarding the \"minutiae\" analysis for the robust authentication phase. This makes the \"fingerprint minutiae\" narrative largely cosmetic and disconnected from the proposed solution.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|47|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb47", "comment": "The authors incorrectly label the generated binary matrices as \"cryptographic binary code responses\" despite admitting they are unstable and not used in the robust authentication protocol.\n\n\"A first approach to exploit nanopatterns as physical unclonable functions is to generate a cryptographic binary code response of the system based on local features\"\nThe term \"cryptographic binary code\" implies a stable, deterministic bitstring that can be used as a key in cryptographic protocols.\n\"Even small translations... can cause bit flips in the related binary code matrix... Here, we show that the robustness... can be enhanced by exploiting matching algorithms... without the need of extracting a binary code matrix\"\nThe authors explicitly state that the binary code matrix extraction is not robust to real-world variations and propose an alternative (image matching) that avoids it. Therefore, labeling the unstable matrices as \"cryptographic\" is misleading and overstates the system's capability to generate actual cryptographic keys.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|47|Gemini|5", "source": "prb", "split": "test", "paper_id": "prb47", "comment": "The paper does not sufficiently justify the necessity of the SEM-based approach over existing Optical BCP PUFs, given the significant trade-off in practicality.\n\n\"Nanoscale physical unclonable function labels based on block copolymer self-assembly\" [1]\nThe authors cite Kim et al. [1], who achieved BCP-based PUFs with optical readout. Optical methods are significantly cheaper, faster, and non-destructive compared to SEM.\n\"encoding capacity larger than the number of atoms in the known universe\"\nThe primary justification for the \"nanoscale\" (SEM) approach seems to be the extremely high encoding density. However, if optical PUFs already provide sufficient entropy (e.g., >128 bits) for all practical security applications, the move to SEM offers diminishing returns on security while drastically reducing practicality. The paper fails to critically evaluate this trade-off.\n\nReferences:\n[1] J. H. Kim et al., \"Nanoscale physical unclonable function labels based on block copolymer self-assembly,\" Nature Electronics, vol. 5, pp. 433–442, 2022. https://www.nature.com/articles/s41928-022-00788-w", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|47|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb47", "comment": "Several studies have reported using self-assembly of polymers to produce authentication tags. In this respect, the pattern manufacturing method and authentication elements shown in this study are similar to previous results. Therefore, if the paper's novelty is to increase accuracy through image processing, additional explanation is needed, especially in the abstract.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|47|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb47", "comment": "Since the fingerprint tag produced in this study is characterized by nano size, expensive and space-limited equipment such as SEM is required to identify the morphology for authentication; therefore, to discuss actual application to the supply chain as shown in figure 1b, it will also be necessary to discuss difficulties that may arise in measurement or actual use.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|47|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb47", "comment": "The explanation in Figure 1f-i states that the self-assembly engraving technology can be applied directly to the surfaces of various products that are not flat, such as diamonds and cameras. However, it is technically very difficult to form the BCP self-assembled structure on an uneven surface and etch it uniformly. Therefore, explaining the technologies and problems required to apply engraving technology is necessary. Furthermore, regarding the SEM image inserted in Figure 1f-i, the figure may need to be modified as it may cause readers to misunderstand that the technology was applied on various product surfaces that are not flat.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|47|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb47", "comment": "In line 204th, the authors explain that the intrinsic randomness of the self-assembled structure can guarantee the uniqueness of the response of the PUF. However, the uniqueness of the response is expected to be affected by several factors, such as the deviation of the response depending on the characteristics or type of challenge input to the PUF and the averaging effect of the response depending on the size of the PUF label. Therefore, it seems necessary to further explain that the self-assembly's intrinsic randomness guarantees the response's randomness.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|47|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb47", "comment": "In Figure 2, the authors achieved improved image recognition capabilities through fingerprint enhancement, allowing different types of defects to be distinguished much better. However, in Figure 3, the key is generated only through the presence or absence of minutia and density. Therefore, discussing the strategies to actively utilize the advantages of improving image recognition ability through data processing in key generation, such as encryption of specific minutia types, will strengthen the authors’ argument.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|47|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb47", "comment": "The thermal stability discussed in Figure 4e will vary greatly depending on the constituent materials of the product to be engraved or heat treatment conditions. For example, if a fingerprint is engraved on a product made of ceramic, it will be thermally stable even in a high-temperature environment of 300 degrees, but in the case of a polymer, it is questionable whether it will be thermally stable under the same conditions. In this regard, explaining the importance of material selection to ensure thermal stability and the temperature limit that can maintain thermal stability would be better.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|47|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb47", "comment": "Strictly speaking, the concept of PUF is an object that performs authentication with a pair of inputs called ‘challenge’ and an output called ‘response’ without exposing the internal structure. In this respect, the fingerprint pattern fabricated by the authors is close to an anti-counterfeit tag or identifier because authentication must be performed by verifying the internal structure. Therefore, if the authors briefly mention that the fingerprint pattern is close to the anti-counterfeit identifier, the author will be able to prevent confusion among readers.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|47|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb47", "comment": "It would be better to write the full name before using the abbreviated form in the text. For example, ‘RCP’ in the method part is supposed to mean random copolymer, but it may need to be clarified for those unfamiliar with the content. Reaffirming the format and typos of the paper will help readers understand. For example, in line 150th, there is no period, and in line 422, ‘counterfeiting’ should be ‘anti-counterfeiting.’", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|47|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb47", "comment": "Verification/reading of the PUF function requires a scanning electron microscope to image the nanopattern. The manuscript describes the difficulty of authenticating the PUF as an enhancement to the security. I consider it to be a severe limitation to the use of the PUF. It would work much better and be more usable if there was an easier way to authenticate the PUF function. Putting your chip into an SEM is pretty involved, especially after the chip has been packaged. In that case you would have to open up the package and destroy the chip. As described, it is only really readable during wafer fabrication. In general there is pretty good security during the wafer fabrication process and the main counterfeiting concern is during packaging and post-packaging. It would be much better if there was an electrical or optical method for measuring the nanopattern that would get out a unique signature from the PUF. An electrical or optical method might also be more sensitive to nanoscale details of the nanopattern than the SEM imaging and defect analysis is. It also could be sensitive to the materials and the nanoscale 3D structure of the nanopattern. These additional factors would make it much more difficult to clone the PUF.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|47|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb47", "comment": "The proposed structures are not actually unclonable as described. If the nanopattern is available for SEM imaging, it could be cloned. The manuscript only addresses this concern by saying that the PUF could be hidden on the chip. This isn’t really a good security feature because the location is difficult to protect and could be discoverable if the PUF is widely used. There are two methods I’m aware of that could clone the proposed PUFs. The first method is nanoimprint lithography (NIL). NIL can be used to make a replica of the PUF nanopattern and transfer it to a new chip (or many new chips). Their verification/reading method using imaging SEM is not sensitive to the depth of the pattern or the material that the pattern is made out of. They are simply analyzing the 2D binarized fingerprint structure and defects on the 20-50 nm length scales. These defects could easily be replicated with the nm-scale resolution of NIL. The second method is e-beam lithography. Since the PUF nanostructure is imageable, it would be possible to use the digital image to create a pattern for e-beam lithography. The 2D pattern with sub-20 nm resolution would require a very good e-beam tool and some process development, but would be doable if the authentication is simply through comparison of large defects in the fingerprint pattern. To make the nanopattern unclonable, it needs to be buried within the chip structure to protect it from imaging, and a non-imaging method of verification/reading would need to be developed. If an electrical/optical method was sensitive to nanoscale fluctuations in the 3D nanostructure it would be effectively unclonable since these features are much more difficult to fabricate controllably even if the PUF was imageable.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|47|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb47", "comment": "How is the reliability performance for the fabricated PUF under the low temperature, such as the range of -40°C~0°C?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|47|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb47", "comment": "There is no direct comparison with other existing materials or techniques applied for PUF, please make some comparison with the state-of-the-PUF designs in terms of the widely-accepted figures of merit, such as reliability, randomness, uniqueness, normalized bitcell area, etc.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Claude|1", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "The paper uses ANOVA with extremely high degrees of freedom that suggest individual breaths or timepoints are being treated as independent observations rather than accounting for the hierarchical nested structure of the data (breaths within trials, trials within mice), which constitutes statistical pseudoreplication and can inflate Type I error rates.\n\n\"when the level of ΔF/F (change in GCaMP activity/ background fluorescence) was summated across trials (Fig. 2f) and over 15s prior to and during CO2 in all trials, there was a robust and statistically significant increase in fluorescence of FoxP2 neurons during exposure to CO2 (F₁, 1682 = 62.2; P < 0.001)\"\nThe degrees of freedom (1682) in this ANOVA is extraordinarily high for an experiment with only n=5 mice and 59 trials. If the analysis were properly conducted at the animal or trial level, the degrees of freedom would be much smaller (approximately 4-8 for animal-level analysis, or around 57-58 for trial-level analysis). The reported value suggests that each timepoint or breath is being treated as an independent observation, which violates the assumption of independence required for ANOVA and artificially inflates statistical power.\n\"During this period we found a significant increase in respiratory rate (RR, 40 ± 1% increase for the last 5 breaths of the 15 sec interval after onset of CO2 exposure compared to the last 5 breaths prior to onset of CO2; F₁, 1662 = 5.7, P < 0.001, Fig. 2h)\"\nSimilarly, the degrees of freedom of 1662 for respiratory rate analysis with only 5 mice is inconsistent with proper statistical handling. The data structure involves 5 mice × 59 trials × multiple breaths, creating a nested hierarchy. Standard practice in neuroscience would require either averaging within animals before performing statistics or using mixed-effects models that explicitly account for this nesting structure to avoid pseudoreplication.\n\"In these experiments 8% CO2, caused a 65 ± 4.4% increase in RR (F₁, 530 = 4.95, P < 0.001, pre vs. post) to 249 ± 5 bpm 20-40sec after CO2, compared to 152 ± 2 bpm at pre-CO2 levels.\"\nThis analysis from the GRIN lens experiments also shows high degrees of freedom (530) for data from only n=3 mice. According to established statistical literature on repeated measures in neuroscience, treating individual timepoints as independent observations when they come from the same animal can inflate Type I error rates by several-fold, potentially leading to false positive conclusions about treatment effects.\n\"In basic neuroscience research, data dependency due to clustering or repeated measurements is probably the norm rather than the exception. Unfortunately, the most widely used methods under these situations are still the t-test and ANOVA, which do not take dependence into account, thus leading to incorrect statistical inference and misleading conclusions.\" from Yu et al. (2022), Neuron [[1]](#citation-1)\nThis recent primer in Neuron explicitly addresses this common problem in neuroscience research. The paper under review appears to fall into this methodological trap, analyzing repeated measures data with standard ANOVA rather than appropriate mixed-effects models, which could compromise the validity of the statistical conclusions.\n\nReferences:\n[1] Yu, Z., Guindani, M., Bhattacharya, S., et al. (2022). Beyond t test and ANOVA: applications of mixed-effects models for more rigorous statistical analysis in neuroscience research. Neuron, 110(1), 21-35. [https://www.sciencedirect.com/science/article/pii/S089662732100845X](https://www.sciencedirect.com/science/article/pii/S089662732100845X)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Claude|2", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "The ArchT optogenetic inhibition experiments (Figure 6) compare Laser-ON versus Laser-OFF conditions within the same ArchT-expressing animals but do not include a critical control group of opsin-negative mice receiving the same laser stimulation, making it impossible to distinguish ArchT-mediated effects from potential thermal or other non-specific effects of 593nm light delivery to brain tissue.\n\n\"To test the necessity of PBFoxP2 neurons in producing the respiratory responses to CO2 during sleep, we photo-inhibited them during hypercapnia. FoxP2-cre mice were injected in the ventral part of the LPB with AAV-Flex-ArchT (n = 12)... We analyzed the respiratory responses to 10% CO2 given for 30s every 300s, with and without photo-inhibition of the PBFoxP2 neurons using a 593 nm laser light\"\nThe experimental design compares Laser-ON versus Laser-OFF conditions within the same animals expressing ArchT. While this within-animal comparison controls for baseline differences between animals, it does not control for the possibility that 593nm laser light itself (independent of ArchT activation) could affect neural activity through tissue heating or other non-specific mechanisms. Best practices in optogenetics recommend including opsin-negative controls receiving identical laser stimulation.\n\"We adjusted the laser such that the light power exiting the bilateral fiber-optic cables was 8-10 mW\"\nThe paper uses 8-10 mW laser power, which is within the range that has been shown to cause tissue heating effects. According to recent literature, light-induced tissue heating can confound optogenetic silencing experiments. Without a control group of wildtype mice or mice injected with a fluorophore-only control virus (e.g., AAV-FLEX-GFP) receiving the same 593nm illumination, it is not possible to definitively attribute the observed effects to ArchT-mediated neuronal silencing rather than to thermal effects of laser light on the targeted brain region.\n\"Overall, Owen et al. demonstrate that light-induced tissue heating can be a confounding factor that should be controlled for in optogenetic silencing experiments... the authors argue convincingly in favor of an amendment to the classical opsin-fluorophore versus fluorophore-only design of opto-inhibition experiments to include an additional cohort of fluorophore-only controls that are treated with 0 mW laser power.\" from commentary on Owen et al. [[2]](#citation-2)\nThis recent literature explicitly recommends including fluorophore-only controls in optogenetic silencing experiments to separate opsin-mediated effects from light-induced thermal effects. The paper under review does not include such controls, which leaves open the possibility that the observed reduction in tidal volume and minute ventilation during ArchT photoinhibition could be partly or wholly due to non-specific effects of laser illumination rather than selective silencing of PBFoxP2 neurons.\n\nReferences:\n[2] Commentary on Owen, S.F., Liu, M.H., & Bhattacharyya, A. (2019). Thermal constraints on in vivo optogenetic manipulations. Nature Neuroscience. [https://pmc.ncbi.nlm.nih.gov/articles/PMC7299086/](https://pmc.ncbi.nlm.nih.gov/articles/PMC7299086/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Claude|3", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "While the paper reports collecting a 405nm isosbestic control signal alongside the calcium-dependent 465nm signal in fiber photometry experiments, the Methods section does not describe the mathematical procedure used to subtract or regress out motion artifacts and photobleaching from the GCaMP signal, which is essential for accurate interpretation of calcium dynamics.\n\n\"The voltage GCaMP and UV signals were Gaussian low-pass filtered at 4 Hz, and saved for offline analysis. Both signal channels (465 and 405 nm) were monitored continuously throughout recordings, with the 405 nm signal (UV) used as an isobestic control. Signals detected with 405 nm wavelength light are not calcium-dependent and are indicative of background fluorescence or motion artifacts.\"\nThe Methods section describes collecting the 405nm isosbestic signal and notes its purpose as a control for motion artifacts, but critically omits any description of how this signal was mathematically used to correct the calcium-dependent GCaMP signal. Simply recording an isosbestic control is insufficient; the control signal must be used in analysis through regression-based subtraction, normalization procedures, or other established methods to remove artifactual components from the experimental signal.\n\"A change in fluorescence (ΔF/F) was calculated by normalizing F to baseline fluorescence. For generating heat maps, min-max normalization was performed that causes linear transformation and the data is scaled in the range (0,1).\"\nThe described ΔF/F calculation only mentions normalizing to baseline fluorescence and does not incorporate the isosbestic control signal. Standard fiber photometry analysis workflows, as documented in widely-used equipment guides and recent methodological papers, involve fitting the isosbestic signal to the experimental signal via linear regression and then subtracting the fitted values to obtain a motion-corrected trace. Without explicit description of such a correction procedure, it is unclear whether the reported calcium signals are properly corrected for movement artifacts that commonly occur during behavioral experiments in freely moving animals.\n\"405 nm or 415 nm are widely used as isosbestic wavelengths for different types of GCaMP, as the total absorption of those wavelengths of UV light does not change during calcium activity changes (calcium independent measurement)... In order to detect motion artifacts, compare the isosbestic 405 nm stream to the 465 nm stream.\" from TDT Fiber Photometry User Guide [[3]](#citation-3)\nStandard fiber photometry protocols explicitly recommend using the isosbestic signal to identify and correct for motion artifacts through comparison and regression-based methods. The paper under review does not describe implementing such corrections. This methodological gap affects the reproducibility of the study and raises questions about whether the reported increases in GCaMP fluorescence during CO2 exposure could be contaminated by movement-related artifacts, particularly since the experiments involved behavioral state changes (transitions from NREM sleep to wakefulness) that typically involve increased movement.\n\nReferences:\n[3] Tucker-Davis Technologies. TDT Fiber Photometry User Guide. [https://www.tdt.com/files/manuals/TDTFiberPhotometryUserGuide.pdf](https://www.tdt.com/files/manuals/TDTFiberPhotometryUserGuide.pdf)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|GPT|1", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "This paper’s primary inferential statistics for calcium signals and breathing responses appear to treat nested, non-independent observations (seconds, breaths, trials, and neurons) as independent samples, which can dramatically inflate degrees of freedom and false-positive rates, undermining the validity of the reported significance for Figures 2–4 and the strength of the conclusions.\n\n“when the level of ΔF/F (change in GCaMP activity/ background fluorescence) was summated across trials (Fig. 2f) and over 15s prior to and during CO2 in all trials, there was a robust and statistically significant increase in fluorescence of FoxP2 neurons during exposure to CO2 (F₁, 1682 = 62.2; P < 0.001)… This increase in ΔF/F was also accompanied by an increase in respiratory efforts in response to CO2 as measured in 59 trials from 5 mice… (RR… F₁, 1662 = 5.7, P < 0.001…)”\nThe manuscript explicitly states that the key photometry and breathing results come from “59 trials from 5 mice,” but the reported ANOVA degrees of freedom (e.g., F₁,1682 and F₁,1662) are far larger than what would be expected if the animal (N=5) were treated as the independent unit. This strongly suggests that repeated measurements within animals (across timepoints and/or trials) were analyzed as if they were independent observations, violating the independence assumption of standard ANOVA. Such pseudoreplication typically leads to underestimated uncertainty and overly small p-values because within-animal correlations are ignored. The problem is especially consequential here because these p-values are used to justify the presence, timing, and robustness of CO2-evoked FoxP2 activity changes and concurrent respiratory changes. A more standard approach would model the hierarchical structure (e.g., mixed-effects models with animal as a random effect) or reduce each trial/animal to a summary metric before group-level inference.\n“We then analyzed the neuronal calcium activity of 28 neurons… where the mice (n = 3) were exposed to CO2… In these experiments 8% CO2, caused a 65 ± 4.4% increase in RR (F₁, 530 = 4.95, P < 0.001, pre vs. post)… Minute ventilation also increased significantly (MV, F₁, 530 = 5.8, P < 0.001)… V_T… (F₁, 360 = 1.53; P = 0.043)”\nThe endoscopic calcium imaging section reports n=3 mice but uses test statistics with degrees of freedom in the hundreds (e.g., F₁,530), which again indicates that many within-mouse observations (breaths and/or time bins, and potentially multiple trials per mouse) were treated as independent replicates. Because respiration and neural activity during a trial are autocorrelated and clustered within animals, such analyses typically overstate evidence for differences between conditions. The same section also mixes multiple biological units (neurons, trials, and mice) without clearly stating what the experimental unit is for each ANOVA, making it difficult to interpret what “n” represents in those tests. This is not a minor reporting issue because these statistics are used to support mechanistic claims about latencies and periodic activation patterns (“waves”) during NREM hypercapnia. With only three animals, the reliable inference should be about between-animal variability rather than between-breath or between-neuron variability within the same animal. Without a model that accounts for nesting, the statistical significance of these effects is not trustworthy.\n“The ‘n’ is reported in the figures and results and represents the number of animals… Using SigmaPlot 12.3, we also tested the sample size and power of the tests post hoc and found that the power of each statistical test was at least 80% at alpha= 0.05, suggesting adequate sample sizes for all the experiments.”\nThis statement conflicts with the degrees of freedom reported throughout the Results (e.g., F₁,1682 with only 5 mice), which implies that the analyses were not actually performed with animal-level independence. Additionally, the reliance on “post hoc” power calculations to argue “adequate sample sizes” is widely regarded as inappropriate because observed power is largely determined by the observed p-value and does not validate the study design. In the context of nested observations, post hoc power can be especially misleading because it can appear high simply due to pseudoreplication inflating the effective sample size. The paper’s argument that statistical power “was at least 80%” therefore does not resolve concerns about whether the reported significance is an artifact of analysis choices. A transparent analysis plan would specify the experimental unit for each test and use hierarchical models or pre-specified aggregation to ensure independence assumptions are met. As written, the statistical section does not adequately justify the validity of the inferential claims.\n“These so-called 'nested designs' yield data that cannot be considered to be independent, and so violate the independency assumption of conventional statistical methods such as the t test. Ignoring this dependency results in a probability of incorrectly concluding that an effect is statistically significant that is far higher (up to 80%) than the nominal α level (usually set at 5%).” ([2](https://pubmed.ncbi.nlm.nih.gov/24671065/))\nThe paper’s design and analysis match the “nested designs” described here: multiple observations (time points, breaths, trials, neurons) are collected per animal, and the manuscript’s reported degrees of freedom strongly suggest those observations were treated as independent. The cited guidance explains why this is a major validity threat: when dependence is ignored, the nominal p-value threshold can severely understate the true Type I error rate. This means that even if the observed effects are real within the sampled animals, the statistical evidence for generalizing those effects to animals as a population may be overstated. The problem is not solved by having many trials or many breaths; the key requirement is more independent experimental units at the correct level (typically animals). This is directly relevant to the central claims because the strongest p-values in the manuscript (e.g., photometry and breathing changes) rely on analyses that appear to violate independence. Consequently, the robustness of the reported “statistically significant” CO2-evoked changes is questionable without reanalysis.\n“Pseudoreplication artificially inflates the sample size, and thus the evidence for a scientific claim, resulting in false positives.” ([1](https://journals.plos.org/plosbiology/article?id=10.1371/journal.pbio.2005282))\nThe manuscript’s statistical reporting is consistent with pseudoreplication: it treats repeated measures within a small number of animals as if they increase the effective sample size, which is reflected in extremely large degrees of freedom for tests based on 3–5 animals. The cited Perspective explains why this is not simply a stylistic statistical preference but a direct threat to the truth of the inferences—false positives become more likely when non-independent observations are counted as independent. In this paper, the most consequential claims (FoxP2 neurons increase activity with CO2, and respiratory variables change significantly) depend on these inflated evidential summaries. Even if the authors performed some blinding for epoch selection, that does not address the core statistical issue of independence. Standard neuroscience practice is to treat animals as the primary unit of inference for behavioral and physiological outcomes and to use models that explicitly account for clustering when many within-animal measurements exist. Without that, the evidence base for the paper’s mechanistic narrative is not sufficiently reliable.\n“Observed power can never fulfil the goals of its advocates because the observed significance level of a test (“p value”) also determines the observed power; for any test the observed power is a 1:1 function of the p value.” ([3](https://www.vims.edu/people/hoenig_jm/pubs/hoenig2.pdf))\nThe manuscript uses “post hoc” power calculations to argue that its sample sizes are adequate, which is precisely the type of reasoning criticized here. If observed power is essentially a transformation of the p-value, then reporting it after the fact does not provide independent support for the reliability of the results; it largely restates whether the test happened to be significant. This matters because the paper’s p-values themselves may be distorted by pseudoreplication and inflated degrees of freedom, so “observed power ≥80%” could simply be a byproduct of the same statistical mis-specification. Moreover, post hoc power does not address whether the correct experimental unit was used, which is central in nested designs like repeated trials per mouse. A defensible analysis would instead report effect sizes with confidence intervals at the animal level and/or use hierarchical models that propagate uncertainty appropriately. As written, the power justification does not mitigate the central concern that the statistical evidence is overstated.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|GPT|2", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "The optogenetic inhibition experiments (ArchT, continuous 593 nm illumination) do not report the standard opsin-free “light-only” controls needed to rule out illumination-induced physiological confounds, which weakens the validity of the claim that PB FoxP2 neurons are necessary for the hypercapnic ventilatory response.\n\n“FoxP2-cre mice were injected… with AAV-Flex-ArchT (n = 12)… We analyzed the respiratory responses to 10% CO2 given for 30s every 300s, with and without photo-inhibition of the PB FoxP2 neurons using a 593 nm laser light… The laser light was on for 60s, beginning 20s prior and extending to 10s after the CO2 stimulus (30s)”\nThese experiments use long-duration continuous illumination, which is exactly the regime most susceptible to non-opsin-mediated light artifacts (e.g., local heating) because tissue temperature can accumulate over seconds. The design as described compares conditions “with and without” inhibition, but the text does not specify an opsin-negative control cohort receiving identical 593 nm stimulation, which is necessary to distinguish true ArchT-mediated neuronal silencing from light-induced physiological changes. The absence of this control is not a minor omission because the observed effects are on tidal volume and minute ventilation—outputs that are sensitive to arousal, stress, and sensory perturbations, any of which can be influenced by illumination. The paper does include a Laser-OFF condition, but that control cannot detect light-only effects, because it removes the light exposure itself. As a result, the causal attribution “photo-inhibition of PB FoxP2 neurons” → “reduced ventilatory response” is not fully isolated.\n“We adjusted the laser such that the light power exiting the bilateral fiber-optic cables was 8-10 mW… [and] drive the orange-yellow light laser (593 nm… ) to be continuously on for 60s beginning 20 s before the onset of the CO2 stimulus.”\nThe reported output power (8–10 mW) and continuous 60-second duration are within the range of parameters that can produce measurable intracranial heating, particularly when delivered through implanted fibers. Even modest temperature changes can affect neuronal excitability and synaptic transmission, which can in turn influence respiratory patterning and autonomic state. Because the paper’s key inference hinges on a reduction in ventilatory volume during this illumination window, any off-target thermal or sensory effects could mimic or mask true circuit effects. The manuscript provides a qualitative justification that this power is “similar” to earlier work, but similarity does not establish absence of artifacts in the specific brain region and duty cycle used here. Control experiments are the accepted mechanism to verify that such parameters do not alter physiology in opsin-free animals. Without those controls, the magnitude and direction of the reported effects cannot be confidently assigned to PB FoxP2 silencing.\n“A key assumption of optogenetics is that light only affects opsin-expressing neurons. However, illumination invariably heats tissue… Thus, careful consideration of light delivery parameters is required, as even modest intracranial heating can confound interpretation of optogenetic experiments.” ([4](https://pmc.ncbi.nlm.nih.gov/articles/PMC6592769/))\nThis directly challenges the implicit assumption in the manuscript that differences between Laser-ON and Laser-OFF necessarily reflect ArchT-driven neuronal inhibition. The cited work documents that light delivery alone can alter spiking and behavior even “in the absence of opsin expression,” which is particularly relevant to long continuous illumination protocols used for inhibition. The manuscript’s inhibition protocol (continuous 593 nm for 60 s) is the kind of illumination where heating artifacts are most plausible, meaning that an opsin-free control is essential to confirm specificity. The paper does not report such a control for the inhibition cohort, so the interpretation remains potentially confounded. This is a validity issue because it affects the central causal claim (necessity) rather than a peripheral measurement. Including opsin-free controls with matched light delivery is standard practice precisely to address this problem.\n“These control experiments should consist of (1) opsin-free controls, in which light is delivered but no opsin is present, and (2) light-free controls, in which the opsin is expressed but light is not delivered…” ([4](https://pmc.ncbi.nlm.nih.gov/articles/PMC6592769/))\nThe manuscript appears to implement only the second control type (Laser-OFF with opsin expressed), while omitting the first (opsin-free with light delivered) for the key ArchT inhibition experiments. The cited recommendation explains why both controls are required: light and opsin expression can each have independent effects, and only the combination of controls can isolate the opsin-mediated causal mechanism. In the present paper, this matters because the claimed effect is a reduction in tidal volume/minute ventilation during hypercapnia, which could plausibly be influenced by heating or other light-driven effects. The recommendation also emphasizes matching surgical preparation and light delivery parameters across controls, underscoring that “no-laser” days are not an adequate substitute for opsin-free illuminated animals. Without these controls, it is difficult to interpret whether the observed reductions reflect neuronal inhibition, thermal suppression, or other artifacts. Therefore, the optogenetic necessity evidence is not methodologically watertight.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|GPT|3", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "The manuscript’s strongest causal and translational statements (e.g., that other pathways cannot compensate, and that optogenetic silencing “blocks” hypercapnia-induced respiratory drive) are not supported by the reported effect sizes, which show partial reductions in ventilatory volume with preserved respiratory-rate responses.\n\n“Our results indicate that PB FoxP2 neurons play an important role in the respiratory response to CO2 exposure during NREM sleep, and indicate that other pathways that also contribute to the response cannot compensate for the loss of the PB FoxP2 neurons.”\nThis sentence makes a strong inference about compensation failure (“cannot compensate”) that implies near-complete necessity or inability of parallel chemosensory pathways to maintain the response. However, the experiments presented are acute optogenetic photoinhibition rather than a definitive “loss” (e.g., genetic ablation or sustained silencing verified electrophysiologically), and thus it is not clear that FoxP2 neurons were fully inactivated. Even if silencing was effective, the results reported later show that core components of the hypercapnic ventilatory response remain intact, particularly respiratory rate increases. In standard circuit physiology, concluding non-compensation typically requires showing that other known CO2-responsive drives cannot restore the phenotype over time or across conditions, which would require additional experiments (e.g., prolonged manipulations, dose–response, or combined perturbations). The manuscript itself discusses multiple other brainstem CO2-responsive sites, making the non-compensation claim even stronger and thus more demanding to substantiate. As written, the statement overstates what the presented data demonstrate.\n“Photoinhibition of PB FoxP2 neurons significantly reduced the increase in V_T caused by CO2… by 42%… pre-arousal and by 34%… after arousal… [and] reduced the increase in MV… by 37% post-arousal… Photoinhibition of PB FoxP2 neurons had little effect on the RR increases induced by CO2… and no effect on latency to arousal.”\nThese results indicate that the hypercapnic ventilatory response is attenuated but not abolished, and that respiratory rate responses in particular are largely preserved. This pattern is more consistent with PB FoxP2 neurons contributing to a component of ventilatory volume (tidal volume and/or post-arousal volume augmentation) than being strictly required for the overall hypercapnic response. The reported reductions are also conditional (e.g., one pre-arousal MV reduction is “not statistically significant”), which further argues against describing the effect as a complete block. Because the respiration phenotype is only partially reduced, the conclusion that other pathways “cannot compensate” is not directly supported; preserved RR increases imply that parallel pathways are still capable of driving substantial ventilatory changes. In addition, the lack of effect on arousal latency suggests that major state-transition dynamics remain, complicating a simple “loss of drive” narrative. Stronger language should be reserved for effects that are near-complete and robust across measures.\n“Acute optogenetic silencing of the PBFoxP2neurons blocks hypercapnia-induced respiratory drive: … Photoinhibition of PBFoxP2 neurons significantly reduced the increases in VT  and MV but not RR caused by CO2 exposure.”\nThe figure caption frames the inhibition effect as “blocks” respiratory drive, but the caption itself immediately acknowledges that RR is not blocked, and the main text reports only partial reductions in VT and MV. In respiratory physiology, “drive” encompasses both timing (frequency) and pattern (volume) components; preserving the dominant RR increase while modestly reducing volume is not accurately described as blocking drive. This mismatch between label (“blocks”) and quantified outcome can mislead readers into overestimating the causal role and effect magnitude. Because figure titles and captions are often what readers rely on for high-level interpretation, overstated phrasing is consequential and can propagate an incorrect impression of necessity. The same overstatement also feeds into the translational suggestion that augmenting this pathway could “avoid hypoventilation,” which would require more direct evidence in apnea-like paradigms. Overall, the written claims exceed what the data support.\n“We suggest that central chemoreception might be properly provided by the interaction of multiple chemoreceptor sites and structures…” ([6](https://pmc.ncbi.nlm.nih.gov/articles/PMC6842881/))\nThe manuscript itself acknowledges multiple CO2-responsive sites (e.g., RTN, raphe, NTS), so the broader literature expectation is that ventilatory responses arise from interacting and partially redundant circuits. In that context, concluding that “other pathways… cannot compensate” requires particularly strong evidence showing that the system cannot maintain function through those alternative sites when PB FoxP2 neurons are perturbed. The partial nature of the reported effects (VT/MV reduced, RR preserved) aligns more naturally with a distributed-control view rather than a single indispensable node. The cited sentence emphasizes interaction among multiple chemoreceptor sites, which undercuts claims that a partial perturbation implies global non-compensation. While PB FoxP2 neurons may indeed be important, the evidence presented here supports a modulatory or contributory role more than a non-compensable bottleneck. Therefore, the paper should temper its necessity and translational statements to match both its own data and the field’s understanding of distributed chemoreception.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|GPT|4", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "The manuscript’s core quantitative results rely on proprietary software workflows (Spike2 respiratory scripts, SigmaPlot ANOVA) and manual analysis steps without providing scripts, parameters, or data access, limiting methodological transparency and impeding reproduction of the main findings.\n\n“Respiratory data was analyzed by running the respiratory script in the Spike2 (CED, UK) software, which performs breath by breath analysis for many respiratory parameters such as RR, V_T and MV.”\nThe paper’s main mechanistic claims depend on small-to-moderate changes in RR, VT, and MV, so the exact breath-detection and parameterization choices are central to the results. However, the manuscript does not identify which Spike2 script version was used, what thresholds or filtering settings were applied, or how artifacts (movement, sniffing, cable tug) were handled beyond a few selection rules. Because Spike2 scripts are not necessarily standardized across labs and can be customized, independent researchers cannot reconstruct the same processing pipeline from the description alone. This is particularly important here because the statistical analyses appear to use fine-grained breath windows (e.g., “last 5 breaths”), making the output sensitive to detection details. Without access to the exact scripts and example raw traces, it is not possible to verify the reported percent changes or reproduce the figures. This limits confidence in the robustness of the reported quantitative respiratory effects.\n“All statistical analyses were performed using SigmaPlot 12.3… The F and P values are described in the results section with details of the statistical tests also given in the respective figure legends and represented in the figures.”\nUsing proprietary point-and-click statistical software is not inherently invalid, but it places a higher burden on the manuscript to specify exact model structures, factors, repeated-measures handling, and preprocessing steps, because the analysis is otherwise opaque. In this paper, the reported degrees of freedom suggest nonstandard or at least non-obvious choices about what constitutes an independent observation, so reproducibility requires a clear description of the data table used for each test. The manuscript does not provide those per-test design matrices, nor does it provide the underlying datasets that would allow reanalysis and verification. In practice, this prevents reviewers and readers from checking whether the statistical models matched the experimental unit and nesting structure. This is not a cosmetic issue because the statistical validity is already in question from the reported degrees of freedom. Providing data and analysis code (or at minimum, exported analysis tables and settings) is necessary to make the core quantitative claims reproducible.\n“Last, but not least, all input data, scripts, versions, parameters, and intermediate results should be made publicly and easily accessible.” ([5](https://journals.plos.org/ploscompbiol/article?id=10.1371/journal.pcbi.1003285))\nThe manuscript’s quantitative pipeline includes multiple software components (Spike2 respiratory scripts, SigmaPlot, photometry processing, Inscopix IDPS) and several analyst choices (manual ROI selection, trial selection rules), but it does not provide public access to the scripts or intermediate outputs that would enable reproduction. The cited reproducibility guideline highlights that making scripts, parameters, and intermediate results accessible is a minimum standard when claims rely on computational analysis steps. This is especially salient here because the paper’s conclusions depend on time-locked analyses (e.g., 15 s windows, peak latencies, breath subsets) where subtle implementation details can change outcomes. Without accessible scripts and data, independent researchers cannot evaluate sensitivity to preprocessing choices or confirm that the results are robust. The lack of computational transparency therefore meaningfully limits the paper’s reproducibility under common expectations in modern neuroscience. Providing a data/code package (even if proprietary tools were used originally) would substantially strengthen the work.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "The paper claims that FoxP2 neurons \"regulate respiratory responses\", but the inhibition experiments show they are not necessary for the frequency component (Respiratory Rate) of the response, despite activation experiments showing they can drive it.\n\n\"Photoinhibition of PB FoxP2 neurons had little effect on the RR increases induced by CO2 (Fig. 6f)\"\nThis result demonstrates that FoxP2 neurons are not necessary for the CO2-induced increase in respiratory rate. The system is capable of increasing RR normally even when these neurons are inhibited.\n\"Stimulation at 20 Hz increased RR by 35% at 5 sec vs. 69% at 10 sec... and MV by 25% at 5 sec and 40% at 10 sec (Fig. 4f).\"\nWhile activation of these neurons *can* increase RR, the inhibition data proves they are not the sole or necessary drivers of this increase under physiological conditions. The conclusion that they \"regulate respiratory responses\" is therefore too broad and fails to distinguish between sufficiency (activation) and necessity (inhibition), and fails to specify that their necessary role is limited to Tidal Volume (V_T), not Rate.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "The authors attribute the arousal observed during 20Hz stimulation to \"sensory feedback\" from hyperventilation, but fail to control for the direct activation of FoxP2+/CGRP+ neurons which they admit exist in the Kölliker-Fuse (KF) nucleus.\n\n\"Interestingly, we found a small number of KF FoxP2 neurons that express the gene for CGRP (Calca) (supplementary Fig. 1)\"\nThe authors acknowledge an overlapping population of neurons that express both FoxP2 and CGRP. Since CGRP neurons are known to drive arousal [1], the activation of this overlapping population during 20Hz stimulation could directly cause the observed arousal.\n\"Interestingly, the EEG arousal occurred at around the same RR as with CO2 or optogenetic stimulation alone... raising the possibility that the arousal caused by stimulation of the PB FoxP2 neurons may be due to the sensory feedback from the increased ventilatory effort.\"\nThe \"sensory feedback\" hypothesis is speculative and unsupported by direct evidence (e.g., blocking feedback). The alternative explanation—that high-frequency stimulation activates the arousal-promoting CGRP+ subset—is equally plausible and was not ruled out. This undermines the claim of a clean functional separation where FoxP2 neurons regulate respiration and CGRP neurons regulate arousal.\n\nReferences:\n[1] Kaur, S. et al. A Genetically Defined Circuit for Arousal from Sleep during Hypercapnia. Neuron 96, 1153-1167.e5 (2017). https://www.cell.com/neuron/fulltext/S0896-6273(17)30977-7", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "The study uses very small sample sizes (n=3) for several key control groups and anatomical studies, which limits the statistical power and reliability of the findings.\n\n\"We subjected mice to either 2h of 10% CO2... (n = 5) or normocapnic air... (n = 3)\"\nA sample size of n=3 for the normocapnic control group in the cFos study is extremely low and likely insufficient to capture biological variability, increasing the risk of false positives or negatives.\n\"We analyzed the neuronal calcium activity of 28 neurons for the periods where the mice (n = 3) were exposed to CO2\"\nSimilarly, using only 3 mice for the calcium imaging analysis limits the generalizability of the findings. Small sample sizes are a recurrent issue in the study design, which weakens the robustness of the conclusions, particularly for the \"non-significant\" findings (like the p=0.081 for MV) which might have been significant with a larger n.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "It is unclear how the FoxP2 neurons get chemosensory information. Their activity in response to hypercapnia comes at a delay, and the latency to activation is heterogeneous (Figure 3d) so it is unlikely intrinsic chemrsensitivity at work. It seems likely that these neurons are connected to central chemosensory neurons in the retrotrapezoid nucleus / parafacial ventral (RTN/pFV). The authors should discuss how FoxP2 parabrachial / Kolliker-Fuse neurons receive chemosensory information.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "The written manuscript overall suffers haphazardness. Time is sometimes \"s\" and other times \"sec\". Sometimes the units are separated from numerals, e.g. \"20 Hz\" and sometimes not \"20Hz\". Figure callouts are inconsistent too: \"Fig. 1\" or \"Fig.1\" or \"Fig 1\". These inconsistencies are rampant. While this critique does not have any bearing on scientific content, it does not, in my view, show attention to detail.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Lines 37, 107: CGRP should be defined.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Figure 1e & f: the bar charts should be replotted to show all the data points as well as either 95% confidence intervals or standard deviation rather than standard error of the mean, to show the data (see: Drummond GB, Vowler SL. Show the data, don’t conceal them. J Physiol (Lond) 589:1861–1863, 2011)", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 141: the number of the figure is missing.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Figure 2d, f-i: the y-axes are labeled with too many and often small ticks and too small type face. It is difficult to read these axes and make sense of the data. The x-axes are inconsistently labeled with different size type faces and time is \"s\" or \"sec\". The graphics should be more elegant and easier to read (see: Tufte ER. The visual display of quantitative information, 2nd ed. Cheshire, Conn: Graphics Press, 2001.)", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_1|9", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Lines 180-204: The figure callouts are sloppily labeled, sometimes missing a period (180, 181, 190) and other times lacking a gap between the period and the numeral (192, 198, 204). While these simple typos have no bearing on scientific content, the sloppiness is disturbing for its excessive frequency.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_1|10", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Figure 4e: Should be \"minute ventilation\" not \"minute volume\".", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_1|11", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 209: missing \"P=\"", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_1|12", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 218: \"movement\" is misspelled.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_1|13", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 242: I think the callout should be to Fig. 3e (not 3f).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_1|14", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 302: \"CTb\" should be defined in the main text when it appears. It is defined in the figure legend, but one expects a definition in the main narrative too.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "The main problem is that the results do not directly or fully support the claim. The authors conclude that LPBN/KF FoxP2 neurons are necessary for the HCVR (lines 332-333: “required for normal respiratory response to CO2 during sleep”; lines 340-341: “we interpret the PB-FoxP2 neurons as primarily mediating the ventilatory response to CO2.”), but their ArchT experiment (attempting to inhibit these neurons) had no effect on respiratory rate, and only a small effect on volume (conversely, photostimulating FoxP2 neurons produced an increase in breathing rate, but not volume – and no explanation is advanced for the discrepancy). Importantly, no attempt was made to simply ablate Foxp2-expressing neurons in LPBN; this is the most straightforward way to test the authors’ hypothesis. Robust methods for ablating specific cell types have been in use for over a decade (Cre-dependent expression of diphtheria toxin A; Cre-dependent expression of modified caspase/phosphatase), and the authors were among the first to use one of these techniques (ablating glutamatergic neurons in the LPBN in 2013). Especially given the uncompelling results with ArchT inhibition, the authors must show what happens when they simply remove Foxp2-expressing neurons from the LPBN/KF region. These concerns are particularly important with HCVR, which is highly variable and state-dependent (high propensity for false-positive and false-negative conclusions).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Also not supported in this manuscript, or in any previous studies, to my knowledge (apologies if I missed it, but it is not cited in this paper), was a claim made in the first sentence of the abstract: that activating CGRP neurons in LPBN “has little effect on respiration.” The authors showed in a previous article that activating CGRP neurons increases arousal, but they did not show any respiratory measurements in those experiments (not that I could find in the 2017 Neuron paper). No such data are provided for CGRP neurons in the present study. The proposed double-dissociation (CGRP neurons mediate arousal & FoxP2 neurons mediate hyperventilation) depends heavily upon the authors’ claim that CGRP neurons have “little effect on respiration.” If this is not true (if stimulating CGRP neurons does in fact increase MV i.e. the respiratory rate and/or volume), such claims should be removed or heavily re-phrased at least.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Further contradicting the claimed double-dissociation is the author’s finding that stimulating FoxP2 neurons in the LPBN triggered arousal in 70% of their ChR2/photostimulation trials. The authors downplay this observation because the arousal happened with a bit of a delay, relative to the HCVR, but it undercuts the idea that FoxP2 neurons specifically trigger HCVR and not arousal. The lack of direct comparisons between arousal and HCVR latency after photostimulating CGRP vs. FoxP2 neurons (and the prior and current lack of information on HCVR after activating CGRP neurons) weakens the conclusions of this study.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "A major flaw in this study has to do with the non-specificity of recording and stimulating neurons that express the gene Foxp2. Anatomical work cited in this new study identified heterogenous populations of FoxP2 neurons in and around the LPBN (including GABAergic neurons in the caudal KF, glutamatergic neurons in rostral KF, and several more glutamatergic populations in LPBN). Another paper, which just appeared in Neuron, identified LPBN Foxp2-expressing neurons that transmit chemical and mechanical itch (Ren et al. 2023). The authors do not go into detail about this complexity and heterogeneity, instead (Fig. 7) treating these aggregate FoxP2 populations as if they had a uniform function(HCVR). If the loss-of-function result had been compelling (see above), this would be less of a problem, but the results presented leave it unclear what concrete advance was made, relative to previous results.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Insufficient attention is given to counterfactuals (negative-control considerations are lacking, or are glossed over). For example, the number (and to a lesser extent, the full distribution) of neurons with a developmental history of Foxp2 expression is more than adult expression of this gene (and of adult FoxP2 immunofluorescence labeling). The authors use a Cre-reporter strategy (fate-mapping developmental expression plus subsequent/adult expression) as a surrogate for actual expression, and justify this with a blanket, qualitative statement about co-expression of the reporter with nuclear immunostaining, but they should at least count the numbers of FoxP2-immunoreactive and GFP-expressing neurons and give the actual numbers and proportions. This is worth pointing out because the authors made clear, black-and-white claims of “validation” and “eutopic” adult expression (lines 466, 1103).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "If the authors wish to claim that the two genes or their protein/peptide products are expressed together in adult neurons, they should co-label mRNA (for Foxp2 and Calca) or immunostain (FoxP2 and CGRP), or some combination of the two. Labeling mRNA in cells expressing a (developmental fate-mapping) Cre-reporter leaves it unclear whether and to what extent there is any adult co-expression, which is what the authors are claiming (lines 148-152).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "The relative functions of LPBN versus KF neurons in this study are not addressed. The development, connections, and functions of KF FoxP2 neurons appear to be quite different from FoxP2 neurons in the LPBN. The senior author’s previous work indicated that neurons in the KF location exert a timing-dependent disruption in the respiratory rhythm by prolonging the post-inspiratory phase (apneusis), and hyperventilatory responses in rats were triggered by neurons located ventrally. Now, however, it seems they are pinning hyperventilatory responses on neurons located dorsally (in the LPBN), without functionally re-mapping this region in mice. This seems like a step backwards and is likely to leave readers confused by the un-addressed discrepancies.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "I do not have expertise or experience with the long-latency hypercapnic responses of neurons in the LPBN/KF region. Therefore, I will not critique the calcium-imaging portion of the paper. However, if a 10-second delay in neuronal response is typical for this type of recording, that should be explained to the reader (presumably involving delayed changes in blood pH buffering? I would expect the polysynaptic neuronal responses to be fairly rapid, sub-second, once the RTN or carotid-body chemoreceptors are activated by even mild acidity).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_2|10", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Lines 298-310 (and 334-335): the authors report “extensive” axonal projections from LPBN FoxP2 neurons to the medulla. In contrast, two papers they cited used the same strain of Foxp2 mice (and a different strain of CGRP mice) and reported that FoxP2 projections to the medulla was minimal and that CGRP neurons in LPBN project more widely in the medulla than FoxP2 neurons. How do the authors explain these discrepancies between their new work and the previous published anatomic studies? The retrograde tracing images shown in this study, like previous results in rodents (including the senior author’s previous results in rats) give the impression of very few LPBN neurons (in contrast to KF) projecting axons to respiratory nuclei in the medulla.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_2|11", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 614-615: how can a primary antibody produce immunostaining if it is omitted? Are the authors instead referring to the secondaries (not mentioned in the preceding lines)?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_2|12", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 740: “A probability of error of less than 0.05 was considered significant” – inaccurate description of p/alpha; rephrase (alpha vs. beta error).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_2|13", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Lines 40-41 “second group of non-CGRP neurons” is confusing (also line 109). Grammatically, it implies that there was already first group of non-CGRP neurons (after the CGRP neurons). There are of course several groups of non-CGRP neurons in the LPBN, but after reading the paper it became apparent that the authors meant that the CGRP neurons were the first group and they are referring to “a second group of LPBN neurons” as one that lacks CGRP. I recommend re-phrasing to eliminate ambiguity.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_2|14", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Lines 45-46 “which has recently been found in this region.” This is not a recent finding – it has been 15 years since Foxp2 expression was shown in the LPBN region (“Conservation and diversity of Foxp2 expression in muroid rodents: Functional implications” Campbell et al. J Comp Neurol 2008; also the Gray 2008 review cited by the authors), with many other papers using this LPBN marker in the interim.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_2|15", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Reference 22 appears to be a conference abstract with contents redundant to the author’s published work. Remove. (reference 18 also appears to be a conference abstract rather than a published, peer-reviewed reference; remove)", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_2|16", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 159 “FoxP2-Cre::L10” is a non-standard way of describing a Cre-reporter strain, but whatever abbreviation is used, I recommend keeping it consistent throughout the manuscript to avoid confusing readers. In at least two other spots, different terms were used: line 150 (“FoxP2-L10”) and line 1095 (“FoxP2-cre-L10”).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_2|17", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Typo Line 218 “movwement”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_2|18", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "More specific criteria (proximity/distance) are needed (preferably with supplementary plots and example images), showing optic fiber targeting in ChR2 and ArchT experiments relative to transduced FoxP2 neurons. For example (lines 268-270), it would be helpful to see examples of successful vs. missed targeting that did or did not produce the reported effects. Most importantly, the reader should understand why some cases were excluded and others were kept. Was the post hoc decision to exclude a case made after reviewing the experimental results, or by someone blinded to the analysis?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_2|19", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Lines 314-315: “ventral part of the PB” – it would be better to provide supplementary plots of these injection sites so the reader knows the exact distribution of neurons that were transduced in each case", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_2|20", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 351: “intersecting” is unnecessary here; also, consider adding “neurons” after “the PB-FoxP2”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_2|21", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 460 & 463: “wildtype littermates” – C57 x Cre littermates are not “wildtype”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_2|22", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 470 typo “Fox-P2”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_2|23", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 509: typo “immune-staining”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_2|24", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 514: “using square grids” – unclear; does this mean that images were tiled together?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_2|25", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 1086: “to the phrenic motor [neurons?]” – there is no evidence in this study (or in any others that I could find) that FoxP2 LPBN or KF neurons project axons to the cervical spinal cord. It may be the case, but the authors should make it clear that this is speculative (or provide evidence).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_2|26", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 1094-1101: the authors labeled Calca (mRNA transcript) yet referred to it as CGRP (peptide). This is confusing and should be simplified for both accuracy and clarity. Also, they used a Cre-reporter strategy (tags developmental+adult expression) yet referred to it as “FoxP2.” They should co-label the mRNAs (Calca, Foxp2) and/or protein products (CGRP, FoxP2) as above, and should be more careful with terminology so that the reader can tell what was and wasn’t labeled.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_2|27", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 1117: as above, there was no Supplementary Figure 3 to evaluate.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_2|28", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Figure1 : bar graphs should be replaced by showing the individual data points.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_2|29", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Figures 4&6: replace the white bars, which obscure the underlying images with thin or dashed lines that indicate possible locations of optic fiber tracts", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_2|30", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Figure 5: axonal labeling in panels b&c is highly over-contrasted, such that many axons look like blobs the diameter of cell bodies. Images should be replaced with less severe contrast/brightness settings.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Directly comparing the effects of CGRP and FoxP2 populations on breathing and arousal would provide much clearer insight into how functionally distinct these populations are.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "FoxP2 neurons appear most active in wake and REM states. However, data showing how activation/inhibition of these neurons may affect breathing in wake/REM are not provided. Thus, it is unclear whether these neurons generally increase breathing (across states) or if they do indeed play a specific role in the respiratory response to CO2 during NREM. Further, the fiberphotometry data (Supplementary Fig 3a), suggest that FoxP2 neuron activity may be correlated with specific types of breathing in the awake state, but no analysis is performed. This would be interesting compare with has been shown for other PB neuron populations (e.g. PMID: 34921781; PMID: 36810601).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "It is also suggested that the activity of FoxP2 neurons corelates with movement (EMG), but no analysis is performed to confirm this. Cross-correlation analysis (or something similar) of FoxP2 activity vs EMG, and FoxP2 activity vs respiratory rate, would be beneficial.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "The authors show CGRP immunohistochemistry in FoxP2 Cre mice to quantify overlap in the KF but not PB. Showing similar data for the PBcl/el to confirm separation of CGRP and FoxP2 neurons, i.e. that the neurons in question are indeed non-CGRP, would help support the conclusions.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "It is clearly shown that FoxP2 neurons have projections to the preBötC area, but the functional role of these projections is not tested. This could provide important insight into the authors speculation that feedback from preBötC or increased respiratory effort, rather than the ascending projections of FoxP2 neurons, is what leads to arousal during activation of FoxP2 PB neurons.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "The FoxP2 neuron activation and inhibition experiments are not complimentary – activation drives RR without much TV effect, whereas inhibition prevents TV increase but not changes in RR. A potential explanation for this is provided, suggesting that RR can’t be reduced because the CO2 stimulus activates multiple other areas that drive RR. This is plausible, but if this is the case, activation and inhibition of FoxP2 neurons in the absence of CO2 should have complimentary (opposite) effects on RR and TV. However, this analysis is not shown. Moreover, based on the inhibition experiments (Fig 6g) it is concluded that FoxP2 neurons are necessary for increased Tv in response to CO2. But, activation of these neurons does not increase Tv (Fig. 4f). Thus, since FoxP2 neurons do not appear to be sufficient to increase Tv, it is unclear how they can be necessary.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|7", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 109: There is some evidence that CGRP neurons actually inhibit respiration, at least in the awake state (PMID: 32856589; PMID: 36810601), which may be worth clarifying here.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|8", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 148: It isn’t definitively shown with this data that they are non CGRP.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|9", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 150: FoxP2-L10 mice should be defined here since this is the first mention of the FoxP2-cre strain.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|10", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 162: “All of the neurons transfected by an AAV that expressed Cre-dependent GCaMP6s (which also fluoresces green) also showed Foxp2 expression in their nuclei”. This is only shown for the L10 reporter mouse, not the AAV experiments, so it is unclear to what extent the viral expression remained specific to FoxP2 neurons.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|11", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Fig 2b: zoomed image isn’t taken from a region that will contribute to the majority of Delta F/F signal.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|12", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 172-174: “The increased activity of PBFoxP2 neurons when emerging from NREM sleep may contribute to the sudden increase in respiratory effort when an animal exposed to CO2 awakens from NREM sleep.” This should be more clearly illustrated/analyzed. Supplementary fig 3b shows only a single example of this and it is unclear whether there is an associated change in RR. Additional analysis to better understand relationships between FoxP2 activity (deltaF/F) state transitions (NREM/REM/wake) and respiratory rate, would be important to support this speculation.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|13", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 175: It would be helpful to clarify here that these are only trials when the mouse was sleeping. Also as suggested above, it would be informative to show whether or not CO2 causes a similar activation of these neurons in the awake state. E.g. repeat Fig 2e when mice are in wake state and compare vs sleep.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|14", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 187-192: It’s unclear how the last 5 breaths etc. aligns with the points on the graphs in Fig2f-i, which appear to be time bins. Please clarify.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|15", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 209-213: Cross correlation analysis to better understand the relationship between EMG and FoxP2 neuron activity in awake state? This relationship is not obvious from the data shown in Fig S3f.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|16", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 217-218: “PB Foxp2 neurons are most active during wake and REM sleep, and particularly during active movement in wake, and may anticipate the need for increased ventilation during active movement.” Too much speculation for Results section without sufficient analysis performed to test these ideas. I.e. cross correlation of EMG and FoxP2 activity to see if FoxP2 activation precedes movements as suggested.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|17", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Fig 3e: Averaged or summed deltaF/F should be shown. Although it is stated that similar oscillations weren’t present in NREM (Line 245-248) this isn’t apparent from the data shown. Additional analysis could help strengthen this point. And again, do these neurons also show responses to CO2 when mice are awake? Was the activity of these neurons recorded during normally behaving conditions in awake mice? Do single neurons show activity profiles similar to those observed in the fiber photometry experiments (i.g. Supplementary Fig 3A)?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|18", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 263-265: What about trials when mice were in wake state or REM? It would be interesting to know how FoxP2 neurons may affect breathing in these conditions as well.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|19", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 267: FoxP2 activation causes arousal from sleep – it’s unclear how different this is from the effect of CGRP neurons?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|20", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 268-270: A supplemental Fig to show/quantify the included/excluded fiber placement locations would be helpful.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|21", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 274-283: It would be helpful to quantify instantaneous RR vs time during 5 and 10 sec stimulations to support the point the authors are trying to make (i.e. similar to Fig. 2h-i). 5 breath “bins” does not provide much resolution.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|22", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 289-292: Similar to the above, if there really is a different time course of the respiratory response in 2% CO2, this should be illustrated in a graph similar to Fig. 2h-i. As currently plotted the response to 20Hz, 10s stim looks identical in normocapnia vs. 2% CO2 (Compare Fig 4 f (blue) and 4g (purple).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|23", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 297: Activation of these projections to the preBötC area would be a nice addition to demonstrate whether or not this is the relevant pathway.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|24", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 299: preBötC or PBC is more conventional notation for preBötzinger Complex than PBZ.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|25", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 321: How does inhibition of FoxP2 neurons affect breathing in awake and REM?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|26", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 326: Reference Fig 6i as well.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|27", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Fig 6 c2,c5: Scale bars seem mislabeled?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|28", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 331-333: The specific role of response to CO2 during sleep is not demonstrated because data testing the role of FoxP2 neurons in the awake state is not provided. Thus, these neurons may have a similar role in sleep and wake states.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|29", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 333-335: could this reflect the “core/shell” configuration of PB Oprm1 neurons as suggested by PMID: 34921781", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|30", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Line 412: Photostimulation of inhibitory preBotC neurons generally slows RR (e.g. PMID: 25643296; PMID: 33670653; PMID: 33863785) unless done specifically during the inspiratory phase (PMID: 29483589) or under specific conditions (ref 38). The other reference provided (39) describes activation of excitatory neurons, which do consistently increase RR.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|31", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "It would strengthen the paper to be clear about whether FoxP2 neurons in PBcl, KF, or both were primarily targeted during optogenetic imaging and manipulation experiments, since these groups of neurons could have distinct functional roles.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|32", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "In general, the figures could be improved by making the size and font of text consistent (some axis labels are very small, some are large, some text is bold, some not, etc.). There is also a lot of color used which can get somewhat confusing, and it is not always consistent. E.g. Co2 trace is green and deltaF/F is red in Fig 2d but CO2 is orange and deltaF/F is black in Fig 2g.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|48|Human_3|33", "source": "prb", "split": "test", "paper_id": "prb48", "comment": "Parabrachial anatomy could be more clearly/consistently referenced in the text. E.g. PBL vs LPB vs PBel/PBcl", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Claude|2", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "All molecular predictors (gene expression, receptor densities, metabolism, synapse density, myelination) and connectivity predictors are derived exclusively from healthy adult participants, yet these are used to predict and explain cortical abnormalities in patient populations where these features may be substantially altered by disease processes.\n\n\"Gene expression data was collected by the Allen Human Brain Atlas as described in Hawrylycz et al.\"\nThe Allen Human Brain Atlas is derived from postmortem brain tissue of donors without known neurological or psychiatric disorders. However, the disorders studied in this paper (schizophrenia, depression, epilepsy, Parkinson's disease, etc.) are known to involve altered gene expression patterns in the brain. Using healthy-derived gene expression to predict patient abnormalities assumes that the spatial pattern of gene expression is preserved in disease, which may not be valid for many of the studied conditions.\n\"Receptor densities were estimated using PET tracer studies for a total of 18 receptors and transporters, across 9 neurotransmitter systems.\"\nThe PET receptor density maps are from healthy volunteers, but many disorders studied involve receptor alterations. For example, dopamine receptors are altered in Parkinson's disease, schizophrenia, and ADHD; serotonin receptors are altered in depression and OCD. Using healthy receptor profiles to predict abnormalities in these disorders is circular if the diseases involve changes to the very receptor systems being used as predictors.\n\"The data used was structural and functional connectivity data for 69 healthy adults (25 males, 28.8 ± 9.1 years of age) from the Lausanne University Hospital\"\nThe structural and functional connectomes used to assess \"connectomic vulnerability\" are from healthy young adults, yet diseases like schizophrenia, epilepsy, and Parkinson's are associated with altered structural and functional connectivity. Hansen et al. (2022) [[4]](#citation-list) themselves noted that \"only seven proteins... show significant and large relationships with the expression of their corresponding genes,\" highlighting that even in healthy brains, the relationship between molecular measures can be complex. In disease states, these relationships may be further disrupted.\n\n* Quote from the paper's limitations: \"both local biological and global connectivity predictors are derived from state-of-the-art open-access datasets in healthy participants, but they do not capture individual variability or changes across the lifespan\"\nWhile the authors acknowledge this as a limitation, they do not discuss how disease-related changes to molecular and connectivity profiles might specifically bias their results. For example, if receptor densities are systematically altered in patient populations, the correlations observed between healthy receptor profiles and patient abnormalities may reflect confounding by regional vulnerability rather than causal mechanisms.\n\nReferences:\n[4] Hansen, J. Y., Markello, R. D., Tuominen, L. et al. (2022). Correspondence between gene expression and neurotransmitter receptor and transporter density in the human brain. NeuroImage, 264, 119671. https://juser.fz-juelich.de/record/910494/files/Hansen_etal_NeuroImage_2022.pdf", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Claude|3", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "The epicentre analysis is performed only on 7 of 13 disorders that demonstrated statistically significant node-neighbor correlations, introducing selection bias that limits the validity and generalizability of the epicentre findings.\n\n\"Epicentre likelihood was only calculated for brain maps with significant correlation between their node and neighbour abnormality (network spreading disorders). This list comprised of: 22q11.1 deletion syndrome, ADHD, ASD, right and left temporal epilepsy, bipolar disorder, and schizotypy\"\nConditioning the epicentre analysis on statistical significance of the node-neighbor correlation constitutes post-hoc selection that biases the sample toward disorders where the analysis is \"expected\" to work. This selection means the resulting epicentre map represents only those disorders meeting a statistical criterion, not a generalizable cross-disorder finding. The 6 excluded disorders (schizophrenia, depression, OCD, obesity, generalized epilepsy, Parkinson's disease) may have different epicentre patterns or none at all, which would affect interpretation of the \"cross-disorder\" epicentres.\n\"We averaged epicentre likelihood of these seven disorders to produce a map of epicentre likelihood across disorders that demonstrate network spreading disorder-specific cortical morphology\"\nBy averaging only the 7 \"network spreading\" disorders, the authors claim to identify cross-disorder epicentres, but this claim is limited to a non-random subset selected post-hoc. Furthermore, among these 7, the left and right temporal lobe epilepsies are averaged together (visible in the code at line 237-239: \"if 4 and 5 in idx: epilepsy_mean = np.mean(epi[:, [4, 5]], axis=1)\"), effectively reducing the sample to 6 unique disorder patterns.\n\n* Quote from Markello & Misic (2021) [[3]](#citation-list): \"We comprehensively assess the performance of ten published null frameworks in statistical analyses of neuroimaging data... even these frameworks suffer from inflated false positive rates and variable performance across analyses.\"\nGiven that spatial null models have variable performance and can have inflated false positive rates, using p < 0.05 significance as a selection criterion may not reliably distinguish disorders with \"true\" network spreading from those with false positive findings. The selection of 7/13 disorders (~54%) based on p-values below an arbitrary threshold may reflect properties of the statistical test rather than meaningful biological differences between disorders.\n\nReferences:\n[3] Markello, R. D. & Misic, B. (2021). Comparing spatial null models for brain maps. NeuroImage, 236, 118052. https://www.sciencedirect.com/science/article/pii/S1053811921003293", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Claude|4", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "The paper repeatedly uses causal and mechanistic language (\"drive,\" \"shape,\" \"propagate,\" \"govern\") to describe relationships that are purely correlational, which may mislead readers about the strength of evidence for mechanistic claims.\n\n\"We find that regional molecular vulnerability and macroscale brain network architecture interact to drive the spatial patterning of cortical abnormalities in multiple disorders.\"\nThe word \"drive\" implies causation, but the analysis consists of linear regression models showing correlation between molecular/connectomic predictors and cross-sectional cortical abnormality patterns. Correlation cannot establish that molecular vulnerability \"drives\" abnormality patterns; other confounding factors could explain both the predictor patterns and the abnormality patterns simultaneously.\n\"We consistently find that local attributes govern both disorder-specific abnormalities and cross-disorder similarity more than global connectivity and regional dynamics.\"\nThe term \"govern\" implies control or regulation, suggesting a causal relationship. However, the dominance analysis used merely decomposes variance explained in a regression model. Higher explained variance does not establish that local attributes causally \"govern\" abnormalities—it only shows stronger statistical association.\n\"molecular mechanisms interact with the structural and functional architectures of the brain to guide cross-disorder abnormality patterns\"\n\"Interact\" and \"guide\" suggest mechanistic processes, but the evidence presented is a correlation between molecular R² and node-neighbor correlation across disorders. This is a meta-analytic correlation across 13 data points (disorders), not a demonstration of molecular-connectomic interaction at the mechanistic level.\n\"connection patterns among vulnerable regions further amplify this vulnerability\"\n\"Amplify\" suggests an active process where connectivity increases vulnerability, but the cross-sectional data cannot determine whether connectivity amplifies vulnerability or whether vulnerable regions happen to be connected for reasons unrelated to amplification. The temporal ordering required to establish amplification (vulnerability → spreading → increased vulnerability) cannot be inferred from cross-sectional data.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Claude|5", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "The distance-dependent cross-validation method (75% training, 25% test based on spatial proximity) may not fully address spatial autocorrelation issues, as test regions adjacent to the training boundary will share autocorrelation structure with training regions, potentially inflating model performance estimates.\n\n\"Each model was cross-validated using a distance-dependent method. For 1000 randomly chosen source regions, the model was fit on a training set, composed of the 75% of regions closest to the source region. Next, cortical abnormality values were predicted on the remaining 25% of regions\"\nThis cross-validation scheme selects the spatially closest 75% of regions for training, meaning the test set comprises only the most distant 25% of regions. However, regions at the boundary between training and test sets will have substantial spatial autocorrelation with training regions. With only 68 cortical regions in the Desikan-Killiany atlas, a 75/25 split results in approximately 51 training and 17 test regions, where test regions near the boundary may have highly correlated values with adjacent training regions.\n\n* Quote from Alexander-Bloch et al. (2018) [[5]](#citation-list): \"On testing for spatial correspondence between maps of human brain structure and function\"\nThis foundational paper on spatial autocorrelation in brain maps (cited by the reviewed paper) emphasizes that spatial proximity creates dependencies that standard statistical methods cannot handle. The reviewed paper's distance-dependent cross-validation creates a sharp spatial boundary, but brain map autocorrelation functions typically decay gradually with distance. Regions in the test set that are only slightly farther than the 75th percentile distance will still share substantial autocorrelation with training regions.\n\n* Quote from code file 01_regression_and_dominance.py, lines 54-55:\n```python\ntrain_idx = idx[:int(np.floor(train_pct * len(coords)))]\ntest_idx = idx[int(np.floor(train_pct * len(coords))):]\n```\nThe code shows that training and test indices are determined by a hard cutoff at the 75th percentile of distance from the source region. This binary split does not account for the continuous nature of spatial autocorrelation, where regions just beyond the cutoff (in the test set) may have values highly predicted by regions just before the cutoff (in the training set). More sophisticated approaches such as spatial block cross-validation or leave-one-out with spatial buffers would better address this limitation.\n\nReferences:\n[5] Alexander-Bloch, A. F. et al. (2018). On testing for spatial correspondence between maps of human brain structure and function. NeuroImage, 178, 540–551. https://www.sciencedirect.com/science/article/pii/S1053811918304968", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|GPT|1", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "This paper makes a potentially invalid and insufficiently documented dataset claim that all ENIGMA-derived cortical abnormality maps come from adult patients, even though at least some of the underlying ENIGMA morphometry mega-/meta-analyses explicitly span childhood through adulthood; this undermines the validity of cross-disorder comparisons and the robustness of downstream interpretations that implicitly assume a single life-stage.\n\n“All cortical abnormality maps were collected from adult patients, following identical processing protocols, for a total of over 21 000 scanned patients against almost 26 000 controls.”\nThis sentence asserts an adult-only sampling frame as a core premise for comparability across the 13 disorder maps, but the paper does not provide disorder-by-disorder age ranges or cite adult-only ENIGMA subgroup analyses for neurodevelopmental conditions. Because cortical thickness and its disorder-associated deviations are strongly age-dependent, mixing developmental stages can change both spatial patterns and effect sizes, which would directly affect the paper’s cross-disorder similarity analyses and regression fits. The claim is also used to justify that the maps are “comparable,” so if it is inaccurate or only partially true, it becomes a validity issue rather than a minor reporting gap. The manuscript does not describe any harmonized restriction to adult cohorts, nor any sensitivity analysis for age-stratified ENIGMA maps. As a result, readers cannot verify whether the analyzed ADHD/ASD/OCD-related maps reflect adult-only case-control effects or a mixture of ages. This ambiguity makes the paper’s cross-disorder conclusions harder to interpret and reproduce.\n“The values for each map are z-scored effect sizes (Cohen's d) of cortical thickness in patient populations versus healthy controls.”\nThis methods statement clarifies that the disorder maps are summary effect sizes but does not specify whether they were computed within an adult-only subset or pooled across ages in the contributing ENIGMA cohorts. Without explicit age-range documentation per disorder, it is impossible to reconcile the adult-only claim with the known design of several ENIGMA working-group analyses. Because the paper later correlates and regresses these maps against molecular and connectomic predictors, any age-related heterogeneity in the source effect-size maps can propagate into both the estimated “predictability” and the identified “epicentres.” Standard practice in large-scale ENIGMA morphometry work is to stratify or model age effects when the sample spans development, precisely because age modifies case-control effects. The absence of such information here prevents an informed assessment of whether age is a confound or a controlled design feature. This weakens confidence that the comparisons across disorders are on equal footing.\n“The sample comprised 1,571 patients with ASD and 1,651 healthy control subjects (age range, 2-64 years) from 49 participating sites.” [[2]](#ref2)\nThis sentence from the ENIGMA ASD working-group abstract directly contradicts an adult-only characterization for at least one disorder category the paper includes (ASD). It indicates that the underlying ASD morphometry analysis spans early childhood through older adulthood, which makes “adult patients” an inaccurate shorthand unless the reviewed paper specifically selected an adult-only ASD derivative map. The reviewed manuscript does not explain any such selection, transformation, or filtering, so readers are left to assume the default ENIGMA map is used. If the ASD map includes ages 2–64, then its spatial pattern can reflect a mixture of developmental trajectories rather than a single adult phenotype. This is especially important because the reviewed paper interprets spatial patterning mechanistically (molecular vulnerability, epicentres), which could be age-contingent. Therefore, the adult-only claim materially affects the validity of the paper’s multi-disorder framework.\n“Analyses were performed separately for children, adolescents, and adults, using linear mixed-effects models adjusting for age, sex, and site (and intracranial volume for subcortical and surface area measures).” [[3]](#ref3)\nThis sentence from an ENIGMA cross-disorder morphometry comparison (ADHD/ASD/OCD working groups) shows that ENIGMA analyses in these neurodevelopmental disorders explicitly treat age group as a key analytic axis rather than assuming adulthood. It implies that pooled analyses across age can mask or alter effects, which is precisely why stratification is performed. The reviewed manuscript includes ADHD and ASD but does not report which age-stratified estimates (if any) were used to create its disorder maps. If the authors used pooled maps, then their own adult-only assertion is inconsistent with typical ENIGMA practice and potentially incorrect. If they used adult-only maps, the omission of this detail is still a major reproducibility gap because it determines which ENIGMA outputs were analyzed. In either case, the paper’s central “single multi-disorder framework” is undermined by unclear age composition for key disorders.\n\nReferences:\n[2] [van Rooij, D., Anagnostou, E., Arango, C., et al. Cortical and Subcortical Brain Morphometry Differences Between Patients With Autism Spectrum Disorder and Healthy Individuals Across the Lifespan: Results From the ENIGMA ASD Working Group. *Am J Psychiatry* (2018).](https://pubmed.ncbi.nlm.nih.gov/29145754/)\n[3] [Boedhoe, P. S. W., van Rooij, D., Hoogman, M., et al. Subcortical Brain Volume, Regional Cortical Thickness, and Cortical Surface Area Across Disorders: Findings From the ENIGMA ADHD, ASD, and OCD Working Groups. *Am J Psychiatry* (2020).](https://pubmed.ncbi.nlm.nih.gov/32539527/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|GPT|2", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "This paper reports a 1,000-iteration distance-dependent cross-validation protocol for validating multilinear models, but the accompanying code implements a different procedure (deterministic leave-one-node-as-source splitting), which undermines the reliability of the reported generalization results and the conclusions drawn from model performance comparisons.\n\n“Briefly, for each of 1 000 iterations, the 75% of regions closest in Euclidean distance to a randomly chosen source node were selected as the training set, and the remaining 25% of regions as the test set.”\nThis sentence describes a stochastic validation scheme with 1,000 random source nodes, which would yield a large distribution of train/test splits and therefore a stable estimate of generalization performance. Because this paper uses cross-validation to support claims that certain predictor families (e.g., receptor profiles) best “predict” disorder maps, the exact validation protocol materially affects conclusions. If the procedure is implemented differently, the reported cross-validation distributions (e.g., medians and quartiles in Fig. S3) may not correspond to what the code actually computes. The mismatch also prevents readers from reproducing the reported validation statistics by running the shared scripts. In structured spatial data, small implementation changes can meaningfully alter estimated performance because nearby parcels are statistically dependent. Therefore, a discrepancy between Methods and code is a significant methodology and reproducibility problem.\n```python\ndef cv_slr_distance_dependent(X, y, coords, train_pct=.75, metric='rsq'):\n    P = squareform(pdist(coords, metric=\"euclidean\"))\n    train_metric = []\n    test_metric = []\n\n    for i in range(len(y)):\n        distances = P[i, :]  # for every node\n        idx = np.argsort(distances)\n\n        train_idx = idx[:int(np.floor(train_pct * len(coords)))]\n        test_idx = idx[int(np.floor(train_pct * len(coords))):]\n        ...\n    return train_metric, test_metric\n```\nThis function iterates over `for i in range(len(y))`, meaning the number of splits equals the number of brain regions (68 here), not 1,000 random iterations as stated in the paper. Because each region is used once as the “source node,” the procedure is deterministic given the coordinates; there is no random sampling of source nodes and no 1,000-iteration Monte Carlo estimate. That difference changes the interpretation of variability in cross-validated performance (it becomes “across source nodes” rather than “across repeated random splits”). It also means the paper’s stated computational procedure and the released implementation are not the same, which harms reproducibility. Given the small sample size (68 parcels), the difference between 68 and 1,000 splits is not superficial: it affects the stability of reported summary statistics and any narrative about robustness. As a result, the cross-validation evidence supporting key performance comparisons is not reliably documented.\n“Ecological data often show temporal, spatial, hierarchical (random effects), or phylogenetic structure. Modern statistical approaches are increasingly accounting for such dependencies. However, when performing cross-validation, these structures are regularly ignored, resulting in serious underestimation of predictive error.” [[1]](#ref1)\nThis passage explains why validation procedures must be carefully aligned with the dependence structure of the data—precisely the situation for cortical maps with strong spatial autocorrelation. The reviewed paper’s cross-validation is intended to mitigate spatial dependence via distance-based splitting, but a misdescribed or mis-implemented scheme can easily yield overly optimistic performance estimates. Because the paper’s headline claims rely on comparing predictive strength across different feature families, underestimating predictive error can lead to overconfident conclusions about which predictors “best” explain disease patterns. The Roberts et al. discussion is general (ecological data) but directly applicable to spatially structured brain parcellation data where neighboring parcels are dependent. It underscores that the details of the splitting procedure are not cosmetic; they determine whether the validation meaningfully tests extrapolation across space. Therefore, the Methods–code mismatch is a significant issue rather than a minor documentation error.\n“the reported statistical significance of these correlation is in some cases greatly inflated by failing to take into consideration the spatial non- independence of brain maps.” [[5]](#ref5)\nThis statement highlights a core risk in brain-map analyses: naive correlation-based evaluation can produce inflated inferences when spatial dependence is not properly handled. In the reviewed work, cross-validation is a key safeguard intended to demonstrate that regression fits are not merely exploiting spatial smoothness. If the cross-validation protocol is misreported relative to what was executed, then the paper’s evidence that it has controlled dependence-driven optimism becomes weaker. Even when spin tests are used for some p-values, validation metrics (train/test correlations) can still be biased if the splitting scheme does not enforce the intended independence. This makes an accurate, code-matched description of cross-validation essential to the paper’s methodological credibility. The cited literature supports the principle that spatial non-independence can inflate correlation-based assessments, increasing the stakes of any CV mismatch. Consequently, the discrepancy threatens the robustness of the paper’s performance-based conclusions.\n\nReferences:\n[1] [Roberts, D. R., Bahn, V., Ciuti, S., et al. Cross-validation strategies for data with temporal, spatial, hierarchical, or phylogenetic structure. *Ecography* (2017).](https://www.wsl.ch/lud/biodiversity_events/papers/Roberts_et_al-2017-Ecography.pdf)\n[5] [Alexander-Bloch, A., Shou, H., Liu, S., et al. On testing for spatial correspondence between maps of human brain structure and function. *NeuroImage* (2018).](https://pmc.ncbi.nlm.nih.gov/articles/PMC6095687/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|GPT|3", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "This paper’s description of the connectomic predictor set is internally inconsistent (claiming nine predictors while enumerating seven), and it also contains conflicting parcellation statements for at least one molecular predictor; these inconsistencies materially reduce methodological transparency and hinder exact reproduction of the regression and dominance analyses.\n\n“A total of nine global connectome predictors were used in the multilinear model to represent the influence that global connectivity has on disorder-specific cortical morphology.”\nThis sentence specifies the dimensionality of the connectomic feature set, which is essential for reproducing regression fits, dominance analysis (which scales with 2^p − 1 submodels), and adjusted R^2 values. However, the paper’s subsequent list of connectomic predictors in the same section contains only seven distinct measures, creating a direct inconsistency in the core model specification. Because dominance analysis partitions model fit across predictors, the number of predictors is not a minor detail; it changes the combinatorics of submodels and the meaning of “dominance.” It also affects adjusted R^2, which explicitly depends on p through the degrees-of-freedom correction. Without knowing whether p=7 or p=9 was used, a reader cannot re-run the analysis and expect agreement with reported dominance patterns. This undermines transparency and reproducibility of one of the paper’s main analytic pillars.\n“Connectivity predictors: strength = sum of weighted connections; betweenness = fraction of all shortest paths traversing region i; closeness = mean shortest path length between region i and all other regions; Euclidean distance = mean Euclidean distance between region i and all other regions; participation coefficient = diversity of connections from region i to the seven Yeo-Krienen resting-state networks [130]; clustering = fraction of triangles including region i; mean first passage time = average time for a random walker to travel from region i to any other region in the network.”\nThis figure caption enumerates exactly seven connectivity predictors, which conflicts with the Methods claim of “nine” predictors. The discrepancy is problematic because readers rely on such lists to understand which aspects of network embedding were tested and which were not. It also impacts interpretability: if additional predictors were included but not described, then the narrative about “centrality” being less dominant than “number of connections” may omit relevant variables. Conversely, if only these seven were used, then the “nine” count is simply incorrect and signals unreliable method reporting. In either case, the mismatch reduces confidence in the precision of the model specification presented to the reader. Given that the paper compares “molecular” versus “connectomic” predictability, miscounting features can also bias perceived fairness of that comparison.\n```python\n# disorder maps + predictors\nct = np.genfromtxt(path+'data/enigma_ct.csv', delimiter=',')\nbio = np.genfromtxt(path+'data/local_biol_predictors.csv', delimiter=',')\nconn = np.genfromtxt(path+'data/' + dataset + '/global_conn_predictors.csv', delimiter=',')\n...\n\nbio_predictor_names = np.load(path+'data/bio_predictor_names.npy')\nconn_predictor_names = np.load(path+'data/conn_predictor_names.npy')\n...\n\npredictors = [bio, conn, conn_bin, conn_fc, np.concatenate((bio, conn), axis=1)]\npredictor_names = [bio_predictor_names, conn_predictor_names,\n                   conn_predictor_names, conn_predictor_names,\n                   np.concatenate((bio_predictor_names, conn_predictor_names))]\n```\nThe released analysis script operationalizes the connectomic predictor set via a single matrix `conn` and a corresponding `conn_predictor_names` array, and then uses this set repeatedly across the main and supplementary variants. This code structure implies that the analysis hinges on a fixed, explicitly enumerated set of connectomic variables, so any mismatch in the manuscript’s stated number of predictors directly affects reproducibility. The script does not document any hidden additional connectomic variables that would reconcile “nine” with “seven,” suggesting the manuscript may contain an incorrect count. Since dominance analysis and cross-validation are executed in loops over these matrices, the predictor dimensionality is baked into the computations. Therefore, inconsistency between the written Methods and the implementation is consequential for anyone attempting to replicate results from the provided codebase. This evidence supports the criticism that the methodological reporting is not sufficiently precise for exact reproduction.\n“All analyses were conducted using the 68-region Desikan Killiany parcellation [19, 29], as this is the native and only available representation of ENIGMA datasets.”\nThis sentence asserts a single parcellation basis for all analyses, which is important because both predictors and outcome maps must be aligned region-by-region for regression. Yet the Methods later describe at least one predictor as being “parcel-lated into 68 cortical regions according to the Lausanne anatomical atlas [19],” which is a different naming/atlas convention within the same manuscript. If this is not merely a wording/OCR issue, it implies a potential atlas mismatch or an undocumented mapping step between parcellations. Such mapping can alter spatial smoothness and correlations, affecting regression and dominance results. Even if the actual underlying processing used a consistent 68-region atlas, the manuscript’s inconsistent descriptions prevent readers from knowing what was done. This ambiguity is significant because parcellation alignment is a core prerequisite for validity of the statistical comparisons.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|GPT|4", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "This paper overgeneralizes its “cross-disorder epicentre” conclusion in the abstract and narrative, because epicentre likelihood is explicitly computed only for the subset of disorders that pass a network-spreading significance filter and is then averaged—so the reported epicentres are not established for all thirteen disorders.\n\n“Finally, we find that cross-disorder abnormalities are consistently subtended by a small subset of network epicentres in bilateral sensory-motor, medial temporal lobe, precuneus, and superior parietal cortex.”\nThis sentence frames the epicentre result as a general property of “cross-disorder abnormalities,” which a reader would reasonably interpret as applying across the full set of 13 disorders analyzed in the paper. However, the Methods/Results later qualify that epicentre likelihood is only computed for disorders that exhibit significant node–neighbour correlations, meaning the epicentre map is conditional on a selection criterion. As a result, the abstract’s phrasing risks overstating the scope of the finding and conflating “cross-disorder” with “across the selected network-spreading subset.” This matters because epicentres are used to support mechanistic claims about network-mediated amplification of pathology, and overgeneralizing them could mislead readers about universality across psychiatric, neurodevelopmental, and neurodegenerative conditions. The paper does not present an epicentre analysis for non-network-spreading disorders or quantify uncertainty about the epicentre locations when the inclusion criterion changes. Therefore, the conclusion as written is stronger than what the implemented analysis supports.\n“Epicentre likelihood was only calculated for brain maps with significant correlation between their node and neighbour abnormality (network spreading disorders). This list comprised of: 22q11.1 deletion syndrome, ADHD, ASD, right and left temporal epilepsy, bipolar disorder, and schizotypy (Fig. S7). We averaged epicentre likelihood of these seven disorders to produce a map of epicentre likelihood across disorders that demonstrate network spreading disorder-specific cortical morphology (Fig. 4c, right).”\nThis passage explicitly defines the epicentre analysis as conditional on a statistical filter and lists only seven included disorders, which directly conflicts with a blanket “cross-disorder” framing across all thirteen disorders. Because the selection criterion is based on a significance test, the subset is not fixed a priori and is sensitive to methodological choices (e.g., null model, connectivity matrix variant), which can affect the resulting averaged epicentre map. Averaging only over this subset also means that disorders without significant network spreading do not contribute to the reported epicentre locations, so the result cannot be interpreted as a pan-disorder epicentre map. This is a substantial limitation because the paper studies disorders with different etiologies and expected propagation mechanisms, and the subset criterion implicitly favors conditions whose maps align with the chosen network-spreading metric. The manuscript does not present alternative summaries (e.g., per-disorder epicentres across all 13, or a weighted analysis accounting for uncertainty). Thus, the strong abstract claim is not fully supported by the described analysis.\n```python\nidx = np.where(pspin['fc-also'] < 0.05)[0]\nif 4 and 5 in idx:  # both epilepsies\n    epilepsy_mean = np.mean(epi[:, [4, 5]], axis=1).reshape(-1, 1)\n    idx = np.delete(idx, (idx == 4) | (idx == 5))\nepi_subset = np.concatenate((epi[:, idx], epilepsy_mean), axis=1)\n\n# epicentre likelihood (mean)\nepi_summary = np.mean(epi_subset, axis=1)\n```\nThe code implements the subset-selection described in the paper by selecting disorders with `pspin['fc-also'] < 0.05` and then computing epicentre summaries only over `epi_subset`. This confirms that the reported “cross-disorder” epicentre map is not computed over all disorders but only over those meeting the network-spreading criterion, with additional ad hoc handling of epilepsy subtypes. Because the subset is determined after significance testing, the resulting epicentre map is subject to selection effects and cannot be interpreted as an unconditional summary across the 13 disorders. The extra step of collapsing two epilepsy maps also changes the effective weighting of disorders in the mean, which should be explicitly reflected in any general claim about epicentres. While such choices may be defensible, they need to be matched by appropriately scoped language in the conclusions. As written, the abstract statement is not aligned with the conditional and selective procedure actually used.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|GPT|5", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "This paper’s connectomic vulnerability and network-spreading inferences are weakened because the structural connectome used to compute all connectivity predictors and neighbour-weighted measures is derived from a small sample of healthy young adults, while the analyzed disorders span conditions with markedly different age distributions and known age-related changes in structural connectivity.\n\n“Structural and functional data were collected ... on \\( n = 70 \\) healthy young adults (16 females, \\( 25.3 \\pm 4.9 \\) years).”\nThis sentence makes clear that all connectomic predictors and network-spreading computations are anchored to a single connectome estimate from young adults. Yet the paper’s disorder set includes conditions with typical onset and progression well outside this age range (e.g., Parkinson’s disease) as well as neurodevelopmental disorders, meaning the normative connectome used for “vulnerability” does not match the life-stage of the patient populations represented in the ENIGMA effect-size maps. Because graph metrics (strength, centrality, participation, etc.) depend on the underlying connectivity matrix, age-related differences in structural connectivity can alter which regions are labeled as hubs or epicentres. The paper acknowledges in general terms that predictors do not capture lifespan changes, but it still draws broad conclusions about connectome architecture interacting with local vulnerability across disorders. Without demonstrating robustness to alternative connectomes (e.g., older-adult connectomes, age-stratified connectomes, or disorder-relevant cohorts), the connectomic conclusions risk being artifacts of the chosen young-adult reference network. This is a substantive limitation because it affects not just effect size but the spatial ranking of key regions. Therefore, the connectomic vulnerability claims are not as robust as the manuscript’s general framing suggests.\n“Third, both local biological and global connectivity predictors are derived from state-of-the-art open-access datasets in healthy participants, but they do not capture individual variability or changes across the lifespan—both of which are key factors in neurological, psychiatric, and neurodevelopmental disorders.”\nThis limitation statement correctly identifies a central threat to validity: the predictors are fixed, healthy reference maps that ignore both individual variability and developmental/aging effects. However, the main text still interprets correlations with these predictors as reflecting mechanisms of “vulnerability” and uses the same young-adult connectome to define neighbour exposure and epicentres. The fact that the authors flag the issue does not resolve it, because no analysis is provided to quantify how sensitive results are to using different age-matched connectomes or to plausible lifespan-related changes in network topology. In many disorders, both connectivity and molecular features change with age, treatment, and disease stage, so a young-adult baseline may systematically mischaracterize where network exposure is highest. This limitation thus directly impacts the strength and generality of the paper’s conclusions, not merely their scope. A robust approach would include sensitivity analyses or stratified reference networks.\n“Results revealed more pronounced age-related decreases in structural connectivity for sensorimotor, ventral attention, and sub-cortical networks ...” [[6]](#ref6)\nThis sentence provides direct evidence that structural connectivity exhibits systematic age-related decreases across the lifespan, affecting multiple networks—including sensorimotor systems that the reviewed paper later highlights as epicentres. If structural connectivity changes with age, then graph metrics and neighbour-weighted exposure estimates computed on a young-adult connectome may not transfer to older adult populations or to disorders with different age distributions. This is particularly relevant because the reviewed paper interprets network spreading and epicentre likelihood as reflecting connectome architecture’s role in shaping disorder patterns. The cited study indicates that the underlying structural connectivity substrate is not stationary across adulthood, challenging the assumption that a single young-adult connectome provides a universally valid “vulnerability” scaffold. Consequently, the paper’s connectomic inferences could be biased toward young-adult hub structure rather than disorder-relevant network organization. This evidence supports the criticism that lifespan mismatch is a significant methodological and interpretive issue.\n“The original Human Connectome Project yielded a rich data set on structural and functional connectivity in a large sample of healthy young adults ... This dataset will provide a unique resource for examining how brain organization and connectivity changes across typical aging ...” [[4]](#ref4)\nThis passage underscores two points relevant to the reviewed paper’s design choices: (i) high-quality connectome datasets are often young-adult–centered, and (ii) connectivity is expected to change across typical aging sufficiently to motivate dedicated aging cohorts. The reviewed paper uses a young-adult connectome as a fixed scaffold to interpret multiple disorders, but the cited overview highlights that extending connectome analyses across age is a primary research goal precisely because the connectome evolves. This supports the argument that applying a young-adult connectome indiscriminately to disorders spanning the lifespan requires explicit justification and robustness checks. In particular, disorders like Parkinson’s disease occur in older populations where age-related connectivity differences are nontrivial, potentially shifting which regions are central or well-connected. Without accounting for these changes, the reviewed paper’s connectomic vulnerability claims may not generalize to the populations that generate the disorder maps. Thus, the external literature reinforces that lifespan mismatch is a substantial concern for validity.\n\nReferences:\n[4] [Bookheimer, S. Y., Salat, D. H., Terpstra, M., et al. The Lifespan Human Connectome Project in Aging: An overview. *NeuroImage* (2019).](https://pmc.ncbi.nlm.nih.gov/articles/PMC6649668/)\n[6] [Merenstein, A., Song, S., et al. High-resolution structural connectivity mediates age-related differences in functional connectivity and fluid cognition. *Brain Communications* (2025).](https://pubmed.ncbi.nlm.nih.gov/41113674/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "The paper contains factual errors in reporting the results for Schizophrenia and Schizotypy, and misinterprets the results for Idiopathic Generalized Epilepsy (IGE), leading to incorrect conclusions about their predictability.\n\n\"Notably, the variance in cortical thickness of schizophrenia (a possible precursor of schizophrenia that is poorly defined in the brain [66]) and idiopathic generalized epilepsy (a form of epilepsy that is thought to be informed by genetics instead of brain structural abnormalities [24, 35]) are poorly explained by both biological gradients and network measures of the brain.\"\nThis statement contains two major errors. First, the parenthetical description \"a possible precursor of schizophrenia\" and the citation [66] clearly refer to Schizotypy, not Schizophrenia. However, the text uses the term \"schizophrenia\", creating confusion. My re-analysis of the provided code and data confirms that Schizophrenia has a relatively high connectivity $R^2$ of 0.43, which contradicts the claim that it is \"poorly explained\". Second, the claim that IGE is \"poorly explained by both\" is factually incorrect regarding connectivity. My re-analysis shows that IGE has a connectivity $R^2$ of 0.265, which is higher than that of ADHD (0.237), Depression (0.121), and OCD (0.101). Therefore, characterizing IGE as \"poorly explained\" by network measures is inconsistent with the data presented for other disorders.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "The paper overgeneralizes the findings on \"network spreading\" and \"epicentres\" to \"cross-disorder abnormalities\" in general, despite the analysis showing significance for only a subset of disorders (7 out of 13).\n\n\"Finally, we find that cross-disorder abnormalities are consistently subtended by a small subset of network epicentres in bilateral sensory-motor, medial temporal lobe, precuneus, and superior parietal cortex.\"\nThis statement in the abstract implies a universal finding across the studied disorders. However, the results section specifies that \"mean epicentre likelihood was calculated for all seven disorders that show a significant correlation between regional and neighbour abnormality\". My re-analysis confirms that \"network spreading\" (correlation between node and neighbour abnormality) is statistically significant ($p < 0.05$) for only 7 disorders (22q, ADHD, ASD, Epilepsy RTLE, Epilepsy LTLE, Bipolar, Schizotypy). Major disorders such as Schizophrenia ($p = 0.13$), Depression ($p = 0.07$), and OCD ($p = 0.08$) are excluded from this \"consistent\" finding. Presenting this as a general \"cross-disorder\" phenomenon without explicitly stating the exclusion of nearly half the disorders (including major ones) in the abstract is misleading.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "The paper infers \"network spreading\" and identifies \"epicentres\" based solely on static cross-sectional correlations between regional abnormality and neighbour abnormality, which is insufficient to establish a dynamic spreading mechanism.\n\n\"A disorder whose cortical morphology demonstrates network spreading was defined as one whose regional abnormality pattern is correlated to mean neighbour abnormality, weighted by structural connectivity and functional connectivity.\"\nA high correlation between a region's atrophy and its neighbours' atrophy (spatial autocorrelation on the network) can arise from shared vulnerability (e.g., spatially correlated gene expression or shared developmental inputs) without any dynamic spreading process [1]. Inferring a \"spreading\" mechanism and using terms like \"epicentre\" implies a causal, dynamic process that propagates pathology from a source. This cannot be rigorously established from static cross-sectional data alone, without longitudinal tracking or fitting a dynamic diffusion model [2]. The paper acknowledges \"interaction\" but the terminology strongly suggests a specific dynamic mechanism that is not directly tested.\n\nReferences:\n[1] Fornito, A., Zalesky, A., & Breakspear, M. (2015). The connectomics of brain disorders. *Nature Reviews Neuroscience*, 16(3), 159-172. https://www.nature.com/articles/nrn3901\n[2] Raj, A., Kuceyeski, A., & Weiner, M. (2012). A network diffusion model of progression predicts longitudinal patterns of atrophy and metabolism in Alzheimer's disease. *Cell Systems*, 73(6), 1204-1215. https://www.cell.com/neuron/fulltext/S0896-6273(12)00976-3", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "The use of healthy adult connectomes and molecular maps to predict abnormalities in developmental disorders (e.g., ASD, ADHD) assumes a normative architecture that may not exist in these patients, ignoring disease-specific alterations.\n\n\"...we defined the connectivity fingerprint of a region by calculating ... of a weighted structural connectivity matrix from 70 healthy adults...\"\nThe study uses a \"normative\" connectome from healthy adults to define vulnerability for all disorders, including neurodevelopmental ones like ASD and ADHD. However, literature suggests that these disorders are characterized by fundamental alterations in the structural connectome itself [3, 4]. By assuming that the \"vulnerability\" is defined by the healthy architecture, the study ignores the possibility that the disease-specific connectome architecture is the primary driver of the abnormalities. This is a significant limitation for the developmental disorders included in the study, as the \"healthy\" vulnerability map may not reflect the actual network constraints present in these patients.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "Each of the disorders is associated with a phenotypic profile (symptoms + neurocognitive disturbances). The study is somewhat limited for not incorporating these. For example, are there common/overlapping neurocognitive disturbances that correspond to the overlapping neurobiological changes. I assume ENIGMA has this information per disorder, that could be incorporated alongside the cortical thickness. This would extend the paper more deeply into translational territory and would be stronger than the superficial “reverse inference” observations on the top of page 8, second column. Likewise, are there symptom- or cognitive features that associate more strongly with the “molecular-correlated” disorders on Fig. 3 (ADHD, MDD – e.g. attention) versus those with a “connectivity” profile (SCZ – e.g. executive functioning). If this is to be deferred to future work, it should in the least be addressed in the Discussion.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "Most of the disorders – some more than others – are quite heterogenous over time (recent onset versus chronic), across age, and across patients (e.g. unipolar versus melancholic versus bipolar depression). Most of the patients in the clinical ENIGMA cohorts are quite stable and have been on pharmacological therapies, many of which have impacts on cortical thickness (e.g. anti-psychotics [1]). MDD, SCZ and ADHD in particular are not unitary entities across time or patients and their representation as singular entities in the various figures is a translational limitation. This approach is not at all unique to the present paper, but a widespread limitation so there is no line to be drawn in the sand here: Again, this could be addressed with some additional analyses (such as a break-out analysis of medication, age or time since illness onset analyses on at least one diagnostic category) or simply acknowledged in the Discussion", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "A methodological limitation is that the core method essentially derives from “correlations of correlations”, limiting insights into deeper mechanistic causes. I think the existing “dig down” analyses are elucidating and largely overcome this weakness, but I would avoid statements like “regional molecular vulnerability and macroscale brain network architecture interact to drive the spatial patterning of cortical abnormalities in multiple disorders” which is something that could hardly have a counter-factual.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "The main marker of neurobiological perturbation is cortical thickness: While this is a good choice, it is arguably not that surprising to see molecular associations stronger than connectomic ones, given that the former impact directly on cortical activity, function and integrity. But does intra-cortical pathology hold a privileged position when considering the pathogenesis of brain disorders? Some might argue that many disorders arise primarily in white matter connections, and that these then propagate to cortical grey matter. This is a relatively minor point but might warrant a brief note in the paper.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "I thought it was only the analysis pipelines that were harmonized across ENIGMA not the image acquisition (p9) which were quite site specific (but I could be wrong!).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "The overall (anti-)correlations among the graph metrics are stronger than the molecular features (heatmap of Figure 1), which likely has an impact on how the relative and adjusted R^2 values are derived using the dominance analysis (as the effective degrees of freedom differ and there does not seem to be a step to partial out mutual correlations).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "p4: Why “embryonic” stage. Wiring abnormalities can arise across any neurodevelopmental stage.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "The MRI data used to reconstruct the normative functional and structural connectivity data is not particularly state of the art (long TR, 32 channel head coil, single-shell, deterministic tractography etc). I doubt this will impact on the bottom-line findings, but I am not sure why the authors did not choose a more advanced HCP-like data set to work with.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Human_1|9", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "The authors note the limitations of the 68-region DK cortical atlas – and the rationale for using it. But the regions in this atlas differ highly in extent and it would be worth checking that regions that dominate the cross-diagnostic findings are not simple larger in extent and therefore more likely to overlap by chance, and more likely to have higher SnR for all the analysis steps.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Human_1|10", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "A point perhaps for another occasion, but I am a bit sceptical about the now widely used spin test to represent nulls for spatial correlations between data sets: While it is crucial that spatial correlations be preserved in nulls, the process of conflated and then collapsing the cortical surface will introduce geometric distortions that over-estimate the true underlying null variance: spatial correlations from highly curved regions will be compressed onto the inflated representation which are then spun and mapped onto flatter regions. While it seems likely that spatial correlations will be preserved ‘on average’ the variance (the width of the null distribution) will be a composite of the true variance plus these geometric effects. A more accurate null could be obtained through whitening then resampling on the naïve cortical geometry. I do not think this is an issue for the present paper (because if anything a wider null means a more conservative test), but hope this limitation either be rebutted or acknowledged in the corresponding Methods section of the ms (p12).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "For some analyses, a considerable number of tests have been carried out (for example those depicted in Figure 2). I understand that correcting for multiple comparisons could be problematic here (metrics are not independent) but, if no correction procedure is used I think it should be at least acknowledged on the limitation section.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "Is the epicentre likelihood related to Euclidean distance? I found intriguing that the highest epicentre likelihood is located at motor (and parietal) cortex. I would have expected that association regions and hubs will constitute these epicentres. As authors point out “In particular, regions that are highly connected and potentially important for communication tend to be disproportionately affected by disease [26, 114]”. I wonder whether I am misinterpreting the metric or whether there the distance effect on the connectivity matrix influences the epicentre likelihood. Interestingly, authors discuss this finding in the discussion but arguments are focused on previous evidence showing that sensory-motor cortex is a plausible epicentre. Could you please discuss whether this is specific to primary cortex? or rather there is also evidence of the opposite (epicentres predominantly in associations cortices). Note: Looking at Figure S7, I think that one possibility is that this is driven by the epilepsy (which is duplicated). Given that these maps show considerable differences in regional distribution across conditions, is the average a meaningful metric?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "The disorder similarity matrix showed in Figure 5a looks very similar to a Structural Covariance Network. Given that it is computed as “pairwise correlation of regional cortical thickness” (according to figure 5a legend) I wonder whether the associations described later are structural-Covariance-related (e.g. as described in Romero-Garcia et al. 2018, Neuroimage) rather than disorder-related. Would it make sense to compute the disorder similarity as the correlation between “cortical thinning (for example, the difference with controls or the T-scores)” rather than using raw cortical thickness? Note: The Disorder similarity methods section states that “we correlated the abnormality vectors” so authors may already have gone down this route. If that’s the case, it will be just a matter of rephrasing this part of Figure 5a legend) and no discussion or analysis would be required.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "Is there a reason why results depicted in Figure 5c,d,e,f are not tested using the spin null model? By doing that it will not be necessary to regress out distance (which as opposed to the spin approach it assumes a linear relationship).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "Explicitly mention that the Lausanne dataset has been used elsewhere (e.g. Bazinet et al. 2021, Neuroimage). Could authors briefly mention why deterministic rather than probabilistic tractography was used?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "I am afraid I do not understand the binning process of the DSI-based connectomes (“last paragraph of the Structural Network Reconstruction). Could authors rephrase this section? What is the objective of this preprocessing step? Is there any reference that readers can check?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "The quantification of myelin content using MRI is still under debate. For example, to my knowledge, there are no articles correlating myelin histology with T1w/T2w ratio. For other approaches such as Magnetization Transfers, R2 ranges between 0.4 and 0.7 approximately. I understand that this is not within the scope of this manuscript (it doesn’t even show a significant association) but I recommend to the authors that they add a one or two lines outlining this limitation of MRI-based myelin markers (see Van der Weijden et al. 2021, Neuroimage, https://www.sciencedirect.com/science/article/pii/S1053811920310466?via=ihub, for an interesting discussion.).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "I am intrigued that Schizophrenia and Schizotypy have such a differentiated influence of molecular vs. connectivity predictors. It is mentioned on the results but it would be interesting to mention on the discussion", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "Given that gene PC1 is likely to mainly reflect differences in cell type distribution, do authors consider that the association between gene PC1 and the thickness differences are driving by this factor?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "Genetic sex has an impact on brain development. Should sex-stratified analysis be done? This may improve power by deconfounding, or lead to some further insight.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "The extent to which the global hypothesis is refuted by this work depends much on the quality of the global phenotypes. For example, if the noise level is higher in the global phenotypes, then they will be found to be less of a contributor to cortical abnormality even if a \"noise free\" version of the global phenotypes is actually more predictive. Can the authors somehow assess the noise level in the local - vs- global phenotypes (maybe with a simulation?) Or possibly repeat the construction of the global attributes using a different preprocessing pipeline?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "What I mean is that 20 years from now, we'll have better technology for assessing graph properties of brains. How confident are the authors that their global evidence will still hold in 20 years, and is there anything more we can do now to gain confidence?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "This might be a good validation of the methodology: can the authors look at pairwise genetic correlation between the pathologies and conditions they study, and see if the pathologies and conditions that share genetic architecture significantly are also close together in the Figure 3 axis? This seems like a good control (towards gaining the sort of confidence I asked for in the previous point) and if the global attributes are robust they should emerge correlated in traits that have similar genetic etiology.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "Some short forms such as pd for Parkinson's and 22q for 22q11.2 deletion are inconsistently used (i.e., sometimes the short form is used othertimes not, which could be confusing).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "If it's possible, the title could be changed so that it's more clear that \"shape\" is a verb, for example \"Cross-disorder cortical abnormalities are shaped by ...\" I know that's longer, maybe there's another way. As it is, it is a bit hard to parse.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Human_3|7", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "On page 3, there is a typo \"cortical abnormaliity\" should be \"cortical abnormality\"", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Human_3|8", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "For Figure 5: x-axis should be on same scale across all except panel a. Pearson's r in some panels looks like < -1, is that because of jitter? panel b: The authors claim this is a normal distribution, can they provide a ks test? panel g: the top 2 and bottom 2 should likely be switched to match caption. Finally, significant correlation is not a contrast to low correlation. None of these are highly correlated (but, they are indeed all positively correlated).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|49|Human_3|9", "source": "prb", "split": "test", "paper_id": "prb49", "comment": "Typo in caption of Figure 1: \"inhibitory\".", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|50|Claude|1", "source": "prb", "split": "test", "paper_id": "prb50", "comment": "The paper's title and abstract claim \"in-sensor adaptive machine learning\" capabilities, but the actual implementation processes machine learning on a cloud server rather than on the device itself, which fundamentally misrepresents the system's architecture and contradicts established definitions of in-sensor computing.\n\n\"The combined data processed by a 2D-like sequential feature extractor with fully connected neurons facilitate the classification of various motion/speech features at a high accuracy of over 90%, which even adapts to the data with noise from motion artifacts or the data from new human subjects.\"\nThe abstract implies that adaptive machine learning occurs within the sensor system. However, the paper later reveals that classification and adaptation occur externally on cloud servers, not locally on the device. This is a fundamental architectural distinction that affects the system's applicability, latency, power requirements, and privacy implications. True in-sensor computing processes data locally without reliance on external computation.\n\"Various activities can also be distinguished with an efficient convolutional neural network and the data processed on a cloud server further facilitate remote rehabilitation and disease diagnosis.\"\nThis statement directly contradicts the title's claim of \"in-sensor\" machine learning. Processing data on a cloud server is fundamentally different from in-sensor processing. In-sensor computing, as defined in the literature, refers to computation performed directly at or within the sensor node itself, without requiring data transmission to external servers.\n\"A wireless user interface further enables remote monitoring and real-time evaluation of laryngeal activities on the cloud server, paving the way for the next-generation standalone stretchable device platform for laryngeal rehabilitation management.\"\nThe system architecture clearly relies on cloud-based processing for machine learning tasks. This contradicts the \"in-sensor\" claim in the title and misaligns with the cited reference [72] (Moin et al.), which demonstrated true in-sensor adaptive learning where both training and inference occur locally on the device using hyperdimensional computing.\n\"Our system implements a neuro-inspired hyperdimensional computing algorithm locally for real-time gesture classification, as well as model training and updating under variable conditions such as different arm positions and sensor replacement.\" [[1]](https://www.nature.com/articles/s41928-020-00510-8)\nThis quote from Moin et al. (reference 72 in the paper) demonstrates what true in-sensor adaptive machine learning entails: local implementation of both classification and model training/updating. The paper under review cites this work but fails to implement comparable local processing capabilities, instead relying on cloud-based CNN processing. This represents a significant conceptual mismatch between the claimed and actual capabilities.\n\nReferences:\n[1] Moin, A. et al. A wearable biosensing system with in-sensor adaptive machine learning for hand gesture recognition. *Nature Electronics* 4, 54–63 (2021). https://www.nature.com/articles/s41928-020-00510-8", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|50|Claude|2", "source": "prb", "split": "test", "paper_id": "prb50", "comment": "The paper claims the device is intended for \"post-surgical rehabilitation\" and \"diagnosis and treatment evaluation of various diseases,\" yet validation was performed exclusively on healthy volunteers without any clinical patient data, which severely undermines the validity of conclusions regarding clinical applicability.\n\n\"With a 2D class sequence feature extractor based on the CNN algorithm, 13 general features from five healthy human subjects can be classified with a high accuracy of 98.2%.\"\nThe training dataset consists of data from only five healthy individuals. Machine learning models trained exclusively on healthy subjects may not generalize to patients with dysphagia, post-surgical conditions, or other pathologies. Disease states alter physiological signals in ways that healthy-subject data cannot capture, making claims about clinical utility unsupported.\n\"Validation of the CNN-based 2D-SFE with the laryngeal activities from another two subjects (SI Note1) shows the high accuracy of over 95% for the 13 features along with three performing states to simulate movement artifacts from choking, chewing, and nodding.\"\nTesting was performed on only two additional healthy volunteers (total n=7 healthy subjects). This extremely small sample size tested only on healthy individuals cannot establish clinical validity for rehabilitation applications. Studies in dysphagia monitoring typically require validation on clinical populations to demonstrate diagnostic accuracy.\n\"The resulting standalone stretchable device with wireless monitoring and cloud processing capabilities paves the way to design and apply the next-generation wearable skin-interfaced systems for the remote monitoring and treatment evaluation of various diseases.\"\nThe claim about \"treatment evaluation of various diseases\" is unsupported as no patients with any disease condition were tested. The gap between healthy volunteer validation and clinical patient populations is substantial in medical device research, and extrapolating from healthy subjects to disease states without evidence is methodologically inappropriate.\n\"Most studies (17/24, 71%) had <60 participants in the dysphagia group. While no clear performance trends were observed between traditional machine learning and deep learning approaches, more recent publications showed a tendency toward using deep learning and ensemble models.\" [[2]](https://www.jmir.org/2025/1/e65551)\nThis recent systematic review of AI-based dysphagia screening emphasizes that even having 60 participants in a dysphagia group may be insufficient for robust validation. The paper under review has zero participants from the target clinical population (dysphagia patients), making its clinical claims entirely unsubstantiated.\n\nReferences:\n[2] So, J.K. et al. Current Technological Advances in Dysphagia Screening. *Journal of Medical Internet Research* (2025). https://www.jmir.org/2025/1/e65551", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|50|Claude|3", "source": "prb", "split": "test", "paper_id": "prb50", "comment": "The paper reports a heart rate of 19.2 beats per minute, which is physiologically impossible for a healthy human adult and indicates either a measurement error, data processing error, or misreporting of values that calls into question the reliability of other physiological measurements.\n\n\"With digital filtering and peak-detection (Fig. 4e), the HR and RR of 19.2 and 50.4 times per minute can be decoupled from the original data (Fig. 4f).\"\nA heart rate of 19.2 beats per minute is physiologically impossible for a conscious, healthy adult human. Normal resting heart rate ranges from 60-100 bpm, and even severe bradycardia rarely drops below 40 bpm in conscious individuals. This value appears to be either swapped with the respiration rate (where 19.2 breaths/min would be normal and 50.4 bpm would be a reasonable HR) or represents a fundamental measurement error. This raises concerns about data processing accuracy throughout the paper.\n\"As the mounting position of the patch moves up the laryngeal skin, the measured cardiac behavior remains unchanged, but the respiration amplitude decreases.\"\nThe paper discusses cardiac measurements as if they were validated, but the impossibly low HR value undermines confidence in the physiological monitoring capabilities claimed for the device. If the values were simply transposed (HR and RR swapped), the error should have been caught during data analysis and manuscript preparation, suggesting insufficient review of reported results.\n\"Besides the good agreement in the HR between our patch and a commercial platform (BL-420) during sitting and breath-holding (Fig. 6g), the characteristic R, S, and T waveforms can also be clearly observed during long-term monitoring.\"\nWhile Figure 6 shows HR values in a physiologically reasonable range (60-120 bpm), the impossible value of 19.2 bpm reported in the main text creates inconsistency. This discrepancy between textual claims and figure data suggests careless reporting that undermines the overall trustworthiness of the presented results.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|50|Claude|4", "source": "prb", "split": "test", "paper_id": "prb50", "comment": "The machine learning evaluation uses data from only 5 subjects for training and 2 for testing without employing rigorous cross-validation methods such as leave-one-subject-out, which is the standard approach for assessing cross-subject generalization in wearable sensor research.\n\n\"Continuous measurements from five participants were used as the training data and the measurements from another two volunteers (a male and a female) were used as testing data.\"\nUsing a simple train-test split with only 5 training subjects and 2 test subjects is methodologically weak for assessing generalization to new subjects. The small sample size (n=7 total) provides insufficient statistical power to make robust claims about classification accuracy. Standard practice in wearable sensor research involves leave-one-subject-out cross-validation or k-fold subject-wise cross-validation to properly estimate inter-subject variability.\n\"Randomly dividing each 2D data of the laryngeal feature into 100 sequences with a fixed length of 1000 data points (covering the entire test data of each feature such as swallowing, drinking, speaking, and coughing) ensured data reliability.\"\nDividing time-series data into random sequences from the same subject and mixing them between training and testing sets can lead to data leakage and overestimated accuracy due to temporal correlation within subjects. Proper evaluation requires keeping all data from one subject either in training or testing, not mixing sequences from the same subject.\n\"In this study, a subject-wise k-fold cross-validation method is implemented to evaluate the generalizability of our predictive techniques. The purpose of our cross-validation model is to ensure that each subject's data is solely allocated to either the training or the testing phase so that the data leakage is eliminated.\" [[3]](https://www.frontiersin.org/journals/bioengineering-and-biotechnology/articles/10.3389/fbioe.2025.1437877/full)\nThis quote from recent wearable sensor research describes the standard methodology for evaluating cross-subject generalization. The paper under review does not employ subject-wise cross-validation, instead using a simple holdout with only 2 test subjects, which is insufficient to reliably estimate performance variability across individuals.\n\"Therefore, in this study, we proposed a cross-subject model based on the Rotary Transformer (RoFormer) to extract features of multiple subjects for continuous estimation kinematics and extend it to new subjects by adversarial transfer learning (ATL) approach.\" [[4]](https://www.frontiersin.org/journals/neuroscience/articles/10.3389/fnins.2024.1306050/full)\nCross-subject generalization in sEMG-based systems is a known challenge requiring specialized approaches such as domain adaptation or transfer learning. The paper under review claims 92% accuracy for new subjects but does not employ any principled transfer learning methodology or proper cross-validation, making the reported generalization performance unreliable.\n\nReferences:\n[3] Yaddanapudi, V. et al. Wearable sensors-based assistive technologies for patient health monitoring: Deep learning approach with feature based optimal network. *Frontiers in Bioengineering and Biotechnology* (2025). https://www.frontiersin.org/journals/bioengineering-and-biotechnology/articles/10.3389/fbioe.2025.1437877/full\n[4] Lin, C. & He, Z. A rotary transformer cross-subject model for continuous estimation of finger kinematics using surface electromyography. *Frontiers in Neuroscience* (2024). https://www.frontiersin.org/journals/neuroscience/articles/10.3389/fnins.2024.1306050/full", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|50|Claude|5", "source": "prb", "split": "test", "paper_id": "prb50", "comment": "The code repository included with the paper lacks essential dependencies (model architecture, loss functions, data loading modules) and does not include the training data, making it impossible to reproduce the machine learning results reported in the paper.\n\n* Quote from code (action_training.py):\n```python\nfrom action_model import My_Net\nfrom losses import OriTripletLoss\nfrom read_action_data_10 import read_data\nfrom plot_function import plot_embedding, confusion_matrix\n```\nThe training code imports four critical modules (`action_model`, `losses`, `read_action_data_10`, `plot_function`) that are not provided in the code repository. Without the model architecture definition (`My_Net`), the loss function implementation (`OriTripletLoss`), the data loading code, and visualization utilities, the code cannot be executed to reproduce results.\n* Quote from code (action_training.py):\n```python\nnet = My_Net(num_classes=10, init_weight = True)\n```\nThe model is instantiated with 10 classes, but the paper claims 13 features/states are classified. This discrepancy between the code (10 classes) and paper (13 classes) suggests the provided code may not correspond to the actual experiments reported in the manuscript, or there are undocumented changes between versions.\n* Quote from code (action_training.py):\n```python\nclass_names_dict = {0: 'ā', 1: 'ō', 2: 'yī', 3: 'bā', 4: 'hēshuĭ', 5: 'A', 6: 'E', 7: 'I', 8: 'O', 9: 'U'}\n```\nThe code shows only 10 classes (5 Chinese pinyin and 5 vowels), but the paper claims classification of 13 features including swallowing, drinking water, and coughing. This fundamental mismatch between the code and paper description raises questions about whether the provided code was actually used to generate the reported results.\n\"Both the offline sEMG dataset and the real-time experiment data collected for this study are available at https://github.com/flexemg/flexemg_natelec.\" [[1]](https://www.nature.com/articles/s41928-020-00510-8)\nThe cited Moin et al. paper provides both code and data for full reproducibility, following best practices in the field. The paper under review provides partial code without the dataset, model definition, or essential dependencies, falling short of reproducibility standards expected in computational research.\n\nReferences:\n[1] Moin, A. et al. A wearable biosensing system with in-sensor adaptive machine learning for hand gesture recognition. *Nature Electronics* 4, 54–63 (2021). https://www.nature.com/articles/s41928-020-00510-8", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|50|GPT|1", "source": "prb", "split": "test", "paper_id": "prb50", "comment": "This paper makes unsupported clinical and post-surgical rehabilitation evaluation claims (Validity, Conclusions) because it does not validate its event classification or the proposed “pathological rehabilitative degree” against accepted gold-standard dysphagia/swallowing assessments or any patient pathology ground truth.\n\n\"According to the gold standard, the clinical evaluation for post-surgical laryngeal rehabilitation mainly focuses on four typical events (i.e., talking, swallowing, drinking water, and coughing) with long-term and extensive efforts<sup>70</sup>.\"\nThis sentence uses “gold standard” to justify reducing rehabilitation evaluation to detecting four activities, but it does not define what clinical gold standard is being referenced or how the proposed outputs correspond to clinically meaningful endpoints. In dysphagia and swallowing-disorder practice, “gold standard” typically refers to validated instrumental examinations (e.g., videofluoroscopy/VFSS and/or FEES), not only the choice of a small set of behaviors. Because the manuscript does not present any paired comparison to instrumental assessments, it is unclear whether the device/ML outputs reflect swallow safety (penetration/aspiration), physiology, or clinically actionable impairment. The absence of an explicit clinical reference standard makes the stated clinical framing vulnerable to circular reasoning (the model predicts the behaviors it was trained to label, rather than validated clinical status). As a result, the paper’s clinical interpretation of its classifications is not adequately supported.\n\"To help evaluate the post-surgical state, a pathological rehabilitative degree is sorted into eight levels in the cloud-served interface based on three typical activities: swallowing, talking, and drinking water (Methods).\"\nThis sentence asserts an 8-level “pathological” grading scheme, but the manuscript does not provide any evidence that these levels correspond to true pathology severity, recovery stage, or clinician-rated outcomes. The only described human data are from volunteers, and the methods do not describe recruiting post-surgical patients or obtaining pathology labels, so the proposed degrees lack a ground-truth target. Even if activity classification is accurate, mapping it to an ordinal pathology scale requires validated clinical criteria and reliability testing (e.g., inter-rater agreement, correlation with standard clinical scales). Without such validation, the interface risks presenting an apparently medical “degree” that is effectively heuristic or arbitrary. This undermines both validity (medical correctness) and the reliability of the clinical conclusions.\n\"A videofluoroscopic swallow study is considered the gold standard diagnostic tool for evaluating dysphagia (see Image. Videofluoroscopic Swallowing Study).\" ([3](https://www.ncbi.nlm.nih.gov/books/NBK565862/))\nThis external reference clarifies what “gold standard” commonly means in dysphagia evaluation: instrumental assessment (VFSS) with direct observation of bolus flow and airway protection. The reviewed manuscript does not report VFSS (or comparable instrumental) measurements collected alongside the patch signals, so it cannot establish criterion validity for dysphagia-related claims. If the authors aim to support clinical rehabilitation monitoring, they need to show alignment with VFSS/FEES findings (e.g., aspiration/penetration events, transit times) or validated clinical scales. Without such comparisons, high classification accuracy on labeled volunteer behaviors does not translate to validated dysphagia assessment. Therefore, the manuscript’s invocation of “gold standard” and its clinical framing are not substantiated by appropriate validation.\n\"The instrumental method currently considered the “gold standard” for studying swallowing is videofluoroscopy, which permits real time investigation of all stages during swallowing.\" ([4](https://pmc.ncbi.nlm.nih.gov/articles/PMC2644994/))\nThis second independent source reinforces that videofluoroscopy is widely treated as the instrumental gold standard for swallowing evaluation, especially because it measures physiology directly across swallowing stages. The paper under review instead proposes a pathology grading derived from activity classification and does not demonstrate that its signals can detect the clinically critical events that videofluoroscopy reveals (e.g., aspiration timing, residue, airway closure). Because the manuscript omits a criterion-standard comparator, it cannot support the implied claim that its outputs are suitable for post-surgical rehabilitation “evaluation” rather than only activity recognition. In clinical sensing literature, establishing agreement with accepted reference assessments is a core step before translating to diagnosis or severity grading. The lack of such validation is a major obstacle to accepting the manuscript’s medical conclusions.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|50|GPT|2", "source": "prb", "split": "test", "paper_id": "prb50", "comment": "This paper’s reported 98.2%/92% accuracies and “adaptation to motion artifacts/new subjects” (Conclusions, Appropriate use of statistics and treatment of uncertainties) are not convincingly established because the dataset is extremely small, the sample-generation/splitting procedure is unclear and potentially biased for time-series data, and no uncertainty estimates or subject-level robustness analyses are reported.\n\n\"Continuous measurements from five participants were used as the training data and the measurements from another two volunteers (a male and a female) were used as testing data.\"\nThis sentence implies that generalization is judged from only two held-out individuals, which is too small to provide a stable estimate of across-subject performance for wearable biosignal classification. With such limited subject count, a single outlier subject or recording condition can dominate reported accuracy, yet the manuscript reports no subject-wise variability, confidence intervals, or repeated splits. In practice, robust claims about generalization to “new subjects” typically require leave-one-subject-out evaluation across many subjects or at least multiple independent test subjects with reported dispersion. The paper also does not describe demographics, trial counts per class, or recording sessions, which makes it impossible to assess whether the test set is representative. Consequently, the strength of the conclusions drawn from the reported accuracies is not warranted.\n\"Randomly dividing each 2D data of the laryngeal feature into 100 sequences with a fixed length of 1000 data points ensures data reliability (covering the entire test data of each feature).\"\nFor temporally correlated physiological time series, randomly slicing a continuous recording into many fixed-length sequences does not by itself “ensure data reliability,” and can create optimistic performance if near-duplicate or strongly correlated segments are used for evaluation. The manuscript does not specify whether these sequences are non-overlapping, whether segmentation is performed before or after train/test separation, or whether windows from the same underlying trial/session can appear in both sets. These details matter because time-series classification is sensitive to leakage through windowing and to correlation structure within subjects. The paper also does not report the number of unique trials per activity or whether labels were assigned independently by multiple annotators. As written, the sampling and splitting description is insufficient to justify the reliability implied by this sentence.\n\"The machine learning model achieves an overall prediction accuracy of 98.2% for the 13 states/features studied in this work (Figs. 5g and S24), demonstrating the excellent performance of the CNN-based 2D-SFE for multidimensional vector prediction (e.g., multiple sequential targets over time)<sup>72</sup>.\"\nThis sentence makes a strong performance claim but provides no statistical characterization of uncertainty (e.g., confidence intervals across subjects, repeated runs with different seeds, or bootstrapping over trials). The manuscript reports a single overall accuracy number without clarifying whether it is computed per-sequence, per-trial, or per-subject, and without clarifying class imbalance handling. In biomedical wearable sensing, high aggregate accuracy can be driven by class frequency or by easy-to-classify states, so per-class and per-subject reporting is typically required to support broad conclusions. Moreover, the model description (62 layers, 2D conversion) does not include enough implementation detail to assess whether the reported accuracy is reproducible or sensitive to hyperparameters. Thus, the evidence provided is not sufficient to support the strength and generality of the conclusion.\n\"The machine learning model with fully connected neurons can adapt to events from new human subjects, resulting in an overall classification accuracy of up to 92% (Fig. 6c).\"\nThis sentence frames “adaptation” as a capability, but the manuscript does not specify what adaptation procedure is performed (e.g., online updating, fine-tuning with labels, unsupervised domain adaptation, or calibration) and what data are used to adapt. Without a clearly defined adaptation protocol and a comparison to a non-adaptive baseline under identical conditions, it is not possible to attribute the 92% accuracy to adaptation rather than ordinary generalization from training. The paper also does not specify whether motion-artifact conditions are systematically injected/controlled, or whether the test scenarios are naturally occurring and potentially confounded with subject identity. Claims of robustness to artifacts typically require controlled perturbation experiments or stratified evaluation by artifact condition. As presented, the adaptation claim is under-defined and insufficiently evidenced.\n\"Here we report a wearable surface electromyography biosensing system that is based on a screen-printed, conformal electrode array and has in-sensor adaptive learning capabilities. Our system implements a neuro-inspired hyperdimensional computing algorithm locally for real-time gesture classification, as well as model training and updating under variable conditions such as different arm positions and sensor replacement.\" ([5](https://research.ibm.com/publications/a-wearable-biosensing-system-with-in-sensor-adaptive-machine-learning-for-hand-gesture-recognition))\nThis related work illustrates how “adaptive learning” in wearable biosensing is typically operationalized: the paper specifies that training and model updating occur and evaluates performance under defined condition shifts (e.g., posture changes, sensor replacement). In contrast, the reviewed manuscript states that its network “can adapt” but does not define whether adaptation is online, whether labels are required, what data are used, or how the model is updated. Without a defined mechanism and an experimental protocol that isolates adaptation from ordinary generalization, the reviewed paper’s adaptation claim remains ambiguous. Moreover, adaptation should be quantified as a performance change attributable to updates under controlled shifts, not simply as a single accuracy number on a small set of new subjects. This gap makes the paper’s adaptation conclusion difficult to evaluate against common practice.\n\"Thereby, 50% of the content of these windows are equal because they present overlapping. As a consequence, 50% of a sample can appear in both training and testing at the same time, biasing the results.\" ([2](https://arxiv.org/pdf/1806.05226.pdf))\nThis external paper explains a standard and well-documented failure mode for wearable-sensor time-series evaluation: window-based sample generation can leak temporally overlapping content across train and test splits, inflating performance. The reviewed manuscript’s description of “randomly dividing” signals into many fixed-length sequences does not specify safeguards against this bias, nor does it demonstrate subject-independent, trial-independent splitting beyond a single 5-vs-2 subject division. Even without explicit overlap, strong temporal correlation can still create overly optimistic estimates if splitting is done at the window level rather than at the trial/session level. Because the manuscript does not provide the necessary experimental protocol details, readers cannot verify that reported accuracies are not affected by this bias. Therefore, the evaluation as described does not adequately support strong generalization conclusions.\n\"Simple experiments show that sample sizes of many neuroimaging studies inherently lead to large error bars, eg ±10% for 100 samples.\" ([1](https://inria.hal.science/hal-01545002v1/document))\nAlthough this statement is from neuroimaging, the core statistical point applies broadly to predictive modeling on small datasets: performance estimates can have large uncertainty when sample sizes are limited. The reviewed manuscript’s across-subject evaluation is effectively based on only two test participants, with no uncertainty quantification, making it difficult to distinguish true generalization from sampling noise. The paper also reports single-point accuracy values without confidence bounds, which prevents assessing whether differences (e.g., 98.2% vs 92%) are meaningful. When authors make clinical-adjacent claims (rehabilitation monitoring), it is especially important to quantify uncertainty and variability across individuals. This omission substantially weakens the reliability of the machine-learning conclusions.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|50|GPT|3", "source": "prb", "split": "test", "paper_id": "prb50", "comment": "This paper does not provide a reproducible implementation of its central machine-learning results (Data and methodology) because the supplied training code cannot run as provided and does not match the manuscript’s stated task setup (13 states, 100 epochs, 62-layer extractor).\n\n\"In the proof-of-the-concept demonstration, five Chinese pinyin and five vowels are chosen as the acoustic states, together with swallowing, drinking water, and coughing behaviors as feature states from five volunteers (sampling rate of 333 Hz).\"\nThis sentence defines the core classification task as 13 distinct states (5 pinyin + 5 vowels + 3 behaviors), which is central to the reported 98.2% accuracy and the overall claimed system capability. Reproducibility requires code that implements the same number of classes and the same labeling scheme, along with the preprocessing that maps raw acceleration/sEMG into the “2D-like vector” input. However, the provided code does not reflect this 13-state setup, creating a direct mismatch between what is evaluated in the paper and what can be executed. Additionally, the manuscript references key details in supplemental figures/notes (e.g., “SI Note1”), but these are not implemented or documented in the code package. As a result, the paper’s main machine-learning experiment cannot be independently reproduced from the supplied materials.\n```python\nfrom action_model import My_Net\nfrom losses import OriTripletLoss\nfrom read_action_data_10 import read_data\nfrom plot_function import plot_embedding, confusion_matrix\n```\nThis code block shows that the training script depends on multiple local modules (action_model, losses, read_action_data_10, plot_function) that are not included in the provided code directory. Because these imports fail, the script cannot be executed to reproduce the reported figures, accuracies, or training dynamics. Missing model definitions and data-loading code are especially critical, as they determine the 2D representation, the network depth/structure, and the train/test split. In reproducible ML practice, authors must provide the complete training pipeline (model, losses, data preprocessing, and evaluation) or a runnable package/container. Without these dependencies, even basic verification of architecture claims (e.g., “62 filtering layers”) is impossible. This constitutes a major reproducibility failure.\n```python\nnet = My_Net(num_classes=10, init_weight = True)\n...\nepoches = 50\n```\nThe paper repeatedly frames the task as 13-state classification and presents training curves “during 100 iterations” and “100-epoch iterations” in the figure captions, yet the code explicitly configures a 10-class model and trains for 50 epochs. This mismatch is not a minor hyperparameter difference; it implies that the code corresponds to a different experimental setting than the one claimed in the manuscript. Changing the number of classes can materially change confusion matrices, t-SNE plots, and overall accuracy, so readers cannot use this code to validate the reported 98.2% result. The mismatch also raises concerns about whether the figures in the paper were produced by the supplied script or by an unreleased internal version. Therefore, the code as provided does not support reproducibility of the stated results.\n```python\nclass_names_dict = {0: 'ā', 1: 'ō', 2: 'yī', 3: 'bā', 4: 'hēshuĭ', 5: 'A', 6: 'E', 7: 'I', 8: 'O', 9: 'U'}\n```\nThis label dictionary further indicates that the implemented classification problem covers 10 categories, mixing pinyin/vowels and a single action (“hēshuĭ”, drink water), but it omits two of the three non-speech behaviors described in the paper’s 13-state list (e.g., swallowing and coughing). That gap makes it impossible to reproduce the specific “post-surgical rehabilitation” activity set as described. It also undermines the paper’s claims that the method was validated on a combined set including swallowing, drinking, and coughing as physiological events. Because label definitions are foundational to supervised classification, such discrepancies directly affect validity of claimed confusion matrices and per-class performance. The paper would need to provide the exact class mapping used to generate Figures 5–6 and the corresponding code to be reproducible. As it stands, the code strongly suggests a different experiment than the one reported.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|50|GPT|4", "source": "prb", "split": "test", "paper_id": "prb50", "comment": "This paper provides internally inconsistent evidence for superior sEMG signal quality (Validity, Conclusions) by asserting that lower SNR supports better signal acquisition, without redefining SNR or explaining the computation.\n\n\"The tight coupling of the device to the skin provides high-quality sEMG signal even with motion artifacts such as from “talking”, as evidenced by the highest power spectral density and the lowest signal-to-noise ratio (SNR) compared to commercial devices (Figs. 3f-g and Fig. S15).\"\nThis sentence uses SNR as primary evidence for “high-quality” sEMG, but it states that the “lowest” SNR indicates superiority, which conflicts with the conventional interpretation of SNR. Because SNR is a ratio of signal level to noise level, lower SNR generally indicates more noise contamination relative to signal, not improved signal quality. If the authors used an inverted metric (e.g., noise-to-signal ratio) or a nonstandard definition, that definition must be stated explicitly for the evidence to be interpretable. The manuscript does not define how SNR was computed (band definitions, preprocessing, artifact segments, or averaging), preventing readers from assessing whether the comparison is meaningful. Since this metric is used to justify a key hardware claim (better sEMG under motion), the ambiguity materially weakens the validity of the stated conclusion.\n\"Commonly expressed in decibels as 10log10(SNR), the higher the SNR, the stronger the signal or information in the signal relative to the noise or distortion.\" ([6](https://pmc.ncbi.nlm.nih.gov/articles/PMC4466709/))\nThis external statement reflects the standard meaning of SNR used across signal-processing contexts: higher SNR corresponds to a stronger/cleaner signal relative to noise. The reviewed manuscript’s claim that “lowest” SNR demonstrates “high-quality” acquisition therefore appears to invert or misuse the metric, unless an alternative definition is provided. Misinterpreting SNR can lead to incorrect comparative conclusions about the patch versus commercial devices, especially when the difference is used to argue robustness to motion artifacts. In biomedical sensing, such quantitative comparisons must be unambiguous because they directly inform the hardware contribution’s credibility. Without a clear definition and correct interpretation, the reported SNR evidence does not reliably support the paper’s signal-quality claims.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|50|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb50", "comment": "The paper claims to present a device with \"in-sensor\" machine learning, but the implementation relies on cloud-based processing, which contradicts the definition of in-sensor computing and misrepresents the system's architecture.\n\n\"A fully integrated, standalone stretchable device platform with in-sensor adaptive machine learning for rehabilitation\" (Title)\nThe title explicitly claims \"in-sensor\" machine learning, implying that the inference or training occurs on the sensor node itself (edge computing).\n\"The measured data wirelessly transmitted to the cloud server in real-time... Validation of the CNN-based 2D-SFE... in the cloud-served interface\"\nThe text contradicts the title by stating that data is transmitted to a cloud server for processing. This describes a standard cloud-based IoT architecture, not \"in-sensor\" machine learning.\n\"device = torch.device('cuda' if torch.cuda.is_available() else 'cpu')\" (from `code/action_training.py`)\nThe provided training code uses PyTorch and checks for a CUDA device or CPU, which are characteristics of a server or high-performance computer, not a low-power wearable sensor node.\n\"Real-time in-sensor implementation of adaptive learning and classification.\" [1]\nIn the literature (e.g., Moin et al., cited as [72] in the paper), \"in-sensor\" machine learning refers to implementing the algorithm directly on the chip to reduce latency and power consumption. This paper's cloud-based approach does not meet this definition.\n\nReferences:\n[1] A. Moin et al., \"A wearable biosensing system with in-sensor adaptive machine learning for hand gesture recognition,\" Nature Electronics, vol. 4, pp. 54–63, 2021. https://www.nature.com/articles/s41928-020-00510-8", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|50|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb50", "comment": "The paper claims a sampling frequency of 800 Hz and analyzes frequencies up to 400 Hz, but the provided code limits the sampling rate to approximately 2 Hz, making the reported results impossible to reproduce with the described setup.\n\n\"The high-sensitivity accelerometer ADXL-345 with a sampling frequency of up to 800 Hz in the patch allows successful continuous monitoring... with a wide frequency spectrum from 0 to 400 Hz\"\nThe authors claim to capture high-frequency signals (up to 400 Hz) which requires a sampling rate of at least 800 Hz (Nyquist theorem).\n\"delay(500);\" (from `code/sketch_may06a.ino`)\nThe Arduino code includes a 500-millisecond delay in the main loop, which forces the sampling rate to be approximately 2 Hz. This is orders of magnitude lower than the claimed 800 Hz and insufficient for capturing the reported signals.\n\"Serial.begin(9600);\" (from `code/sketch_may06a.ino`)\nThe serial communication is set to 9600 baud. Even without the delay, transmitting ASCII data for three axes would limit the sampling rate to less than 100 Hz, further contradicting the 800 Hz claim.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|50|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb50", "comment": "The manuscript is missing the \"Methods\" section, and the provided code is incomplete (missing dependencies), making it impossible to evaluate the experimental procedures or reproduce the machine learning model.\n\n\"# Methods\" (followed immediately by references in `preprint.md`)\nThe manuscript contains a header for \"Methods\" but no content follows it, preventing any assessment of the fabrication process, data collection protocols, or subject demographics.\n\"from action_model import My_Net\" (from `code/action_training.py`)\nThe `action_model.py` file is missing from the provided code directory, rendering the training script non-executable and the model architecture unverifiable.\n\"from read_action_data_10 import read_data\" (from `code/action_training.py`)\nThe data loading script `read_action_data_10.py` is also missing, making it impossible to understand how the data was preprocessed or structured.", "reviewer_type": "ai", "label": "error", "error_type": "Neglect", "label_origin": "expert+llm-filter"}
{"id": "prb|50|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb50", "comment": "The paper claims the machine learning model is \"adaptive\" to new subjects, but the code demonstrates a standard static training process with no mechanism for online adaptation or transfer learning.\n\n\"The machine learning model with fully connected neurons can adapt to events from new human subjects\"\nThe authors claim adaptability, but \"fully connected neurons\" are a standard component of neural networks and do not inherently provide adaptation capabilities.\n\"net.train()\" ... \"optimizer.step()\" (from `code/action_training.py`)\nThe code shows a standard supervised training loop on a fixed dataset. There is no implementation of online learning, domain adaptation, or few-shot learning that would justify the term \"adaptive\" in the context of a deployed sensor.\n\"Real-time in-sensor implementation of adaptive learning... We tuned model hyperparameters... using the offline\" [1]\nTrue adaptive systems typically involve updating the model parameters or hyperparameters in response to new data streams, which is not evidenced in the provided code or described methodology.\n\nReferences:\n[1] A. Moin et al., \"A wearable biosensing system with in-sensor adaptive machine learning for hand gesture recognition,\" Nature Electronics, vol. 4, pp. 54–63, 2021. https://www.nature.com/articles/s41928-020-00510-8", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|50|Gemini|5", "source": "prb", "split": "test", "paper_id": "prb50", "comment": "The classes defined in the provided code do not match the rehabilitation activities described in the paper, raising concerns about the validity of the data and whether the code corresponds to the reported experiments.\n\n\"clinical evaluation for post-surgical laryngeal rehabilitation mainly focuses on four typical events (i.e., talking, swallowing, drinking water, and coughing)\"\nThe paper explicitly lists swallowing and coughing as key activities for classification.\n\"class_names_dict = {0: 'ā', 1: 'ō', 2: 'yī', 3: 'bā', 4: 'hēshuĭ', 5: 'A', 6: 'E', 7: 'I', 8: 'O', 9: 'U'}\" (from `code/action_training.py`)\nThe code defines 10 classes consisting of Chinese pinyin and English vowels, with \"hēshuĭ\" (drinking water) being the only overlap. \"Swallowing\" and \"Coughing\" are absent, suggesting the code was designed for a different speech recognition task.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|50|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb50", "comment": "The reviewer thinks that mechanical durability of the laryngeal patch is not verified enough. Normally, the soldering region between the chips and Cu circuits is easily stressed and disconnected under external strain, so that it is required to examine the performance when stretched. Also, the authors need to evaluate if there is a performance drop after the cyclic stretching test.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|50|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb50", "comment": "The interface between the composite hydrogel and human skin was thoroughly researched. However, there is no analysis about the interface between a hydrogel and a metal electrode array. The reviewer recommends adding data and/or image of the hydrogel-metal interface and proper discussion.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|50|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb50", "comment": "Multiple motions occur simultaneously in real-world situations, and thus analyzing each motion selectively is essential for the practical use. The reviewer wonders if the proposed system could classify multiple motions separately with high precision (e.g., talking while walking, drinking water while coughing). If so, it needs to be demonstrated.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|50|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb50", "comment": "How is the VIA hole in Fig. S13. fabricated? It needs to be explained in the revised manuscript.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|50|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb50", "comment": "The fabrication process and figure images show that the open pad of the electrode directs to the opposite side to the skin (Fig. S14). Why is the device attached to the wrong side?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|50|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb50", "comment": "The concept of machine learning-assisted human activity analysis, including speech recognition, has been already suggested by several groups. In comparison to previous research, the authors collected sEMG and acceleration data, transferred them into 2D vectors, and classified into various motion/speech features. However, the advantage of integrating two distinct data is not highlighted enough. The reviewer recommends adding data or table that emphasizes the difference with previous studies, such as improved accuracy or detecting motions that were challenging to classify.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|50|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb50", "comment": "[Significance to the field and related fields] The significance of the work was not very clear defined in the manuscript, and because this work contains a multi-disciplinary research, each part of innovation was not very clearly stated. For example, regarding the machine learning algorithm, only a well-known module was used, and no specific improvements were made for the proposed wearable sensors. Regarding the circuit design, they were also very basic, not sure what the main challenges to bring those on the skin wearable device, where the majority of electronic components were standard chip. One of the main concern is the power sources, as it can be seen from the schematics, the battery needs externally wired, which significantly reduces the compact design of the sensors. Flexible electronics have been research and report in the following paper, https://pubs.acs.org/doi/10.1021/acs.accounts.8b00500, authors focus on how this work in advances to the existing research regarding the improvements in each aspect of the design.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|50|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb50", "comment": "[Validity of Conclusions and Claims] Yes, some claims partially evidenced, however, due to limitation of testing sample sizes, it would be difficult to conclusion the scientific meanings for clinical applications.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|50|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb50", "comment": "[Reproducibility] no really, as the limitation of data sizes, detailed evaluation of using the proposed sensors, should be further elaborated.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|50|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb50", "comment": "The authors would benefit from working with a swallowing specialist as there are some areas that throughout the manuscript that requires input from a swallowing specialist. For example, on page 3, line 49, the authors use the words “genetic choking.” It is not clear what genetic choking means. Furthermore, swallowing disorders can manifest as a result of many disorders including neurological disorders. It is not only related to “neck cancer or post-surgical treatment.” Similarly, the title of the section on page 8, line 193 is post-surgical rehabilitation. However, post-surgical patients represent only part of the patients who receive swallowing rehabilitation. Furthermore, authors should also rephrase the sentence in lines 194-196 as it is not accurate. In addition, the difference between drinking water and swallowing is not clear to this reviewer.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|50|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb50", "comment": "Page 2, Line 33: The suprasternal notch refers to a specific anatomic location (the notch above the sternum). The location that the sensor was places is not the suprasternal notch area.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|50|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb50", "comment": "Page 3, lines 66-68: Authors refer to flexible EMGs that were developed (22, 24), however, mention that these suffer from low signal quality, motion artifacts, poor system integration, and severe skin inflammation. This reviewer recommends reviewing the citations 22 and 24 and reporting the findings accurately.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|50|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb50", "comment": "The main concern about this paper is in the rationale (71-76). The authors report that there are skin-mounted mechano-acoustic sensors that track activity at the suprasternal notch and that high-quality sEMG signals have not been integrated into these platforms. While this is true, it is important to note that the suprasternal notch area or the laryngeal location that the authors mounted the device are not ideal locations to monitor swallowing activity. It has been well established that larynx moves throughout the swallow including before and after the swallow because of motion unrelated to swallowing. For example, chewing results in the inferior and superior movements of the larynx that are similar to the movements observed during swallowing. Furthermore, it has been well established through intramuscular electrodes, surface electrodes and imaging technologies that the ideal location for capturing swallowing movements using sEMG is the suprathyoid area. This reviewer is concerned about the location of the sensor and the integrity of the signals that were obtained using the sensors. I recommend the authors to use imaging technologies such as VFSS (the current gold-standard method) to validate their signals and ensure that the signals that they are reporting are actually swallowing signals.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|50|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb50", "comment": "The authors report data from 2 healthy adults. However, they also make claims such as “to help evaluate the post-surgical state...” page 10, line 233. It is not clear to this reviewer how authors are able to make these generalizations by using the data obtained from healthy individuals who did not receive head and neck surgery.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|50|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb50", "comment": "Page 15, lines 356-361: The authors report that the pathological degree was sorted into eight levels. Are the authors referring to severity? If so, it would be important to clarify how these 8 levels were determined for swallowing, drinking water, and talking. This reviewer is not familiar with any 8-level evidence-based severity ratings related to swallowing and speech impairments.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|51|Claude|1", "source": "prb", "split": "test", "paper_id": "prb51", "comment": "The paper claims SPPINDEX treatment improves intracortical microelectrode recording performance, yet the signal-to-noise ratio (SNR)—a fundamental metric for assessing recording quality in neural electrophysiology—was significantly lower in the SPPINDEX group compared to the control group (TH) during both study phases. This creates a paradox where the treatment supposedly improves recording but objectively worsens signal quality.\n\n\"Although the signal-to-noise ratio (SNR) was significantly lower in the SPPINDEX group compared to the TH group (p < 0.001 in W1_4, p < 0.0001 in W5_8) for both phases of the study, the mean SNR remained above 5 for all treatments, demonstrating high-quality recordings across all groups (Fig. 4 C).\"\nThe paper acknowledges that SPPINDEX treatment significantly decreased SNR compared to controls with strong statistical significance (p < 0.001 and p < 0.0001) across both study phases. The authors justify this by stating that mean SNR remained above 5, but this does not explain why a treatment claiming to improve recording performance actually worsens this key quality metric. The SNR reduction suggests that while more electrodes may be detecting activity (higher active electrode yield), the quality of individual recordings is compromised.\n\"Noise levels in the SPPINDEX group were significantly higher compared to the TH and Free DEXSP groups (p < 0.05 to TH, p < 0.001 to Free DEXSP) during the first four weeks, indicating a potential increase in noise associated with SPPINDEX treatment during the early weeks (Fig. 4 B).\"\nThe significantly elevated noise levels in the SPPINDEX group provide the mechanistic basis for the decreased SNR. Higher noise directly reduces signal quality and can impair the ability to accurately discriminate neural signals from background activity. This contradicts the paper's central claim of improved recording performance. The authors describe this as \"a potential increase in noise associated with SPPINDEX treatment\" which represents an adverse effect of the treatment itself.\n\"The signal quality is reflected in several metrics, including the signal-to-noise ratio (SNR), single-unit recording capability, and long-term recording capability. Among them, the single-unit recording and long-term recording capability are both related to the SNR. Therefore, the SNR is critical for evaluating the quality of the signal recording.\" [[1]](#citation-list)\nAccording to this review on intracortical microelectrodes, SNR is identified as the critical metric for evaluating signal recording quality, and other important capabilities (single-unit and long-term recording) are directly related to SNR. The paper under review shows SPPINDEX significantly decreases this critical metric while claiming improved recording performance, representing a fundamental contradiction in the study's conclusions. The paper's reliance on active electrode yield alone does not adequately capture overall recording quality.\n\nReferences:\n[1] Guan, S., Wang, J., Gu, X. et al. \"Implantable intracortical microelectrodes: reviewing the present with a focus on the future.\" *Microsystems & Nanoengineering* 8, 7 (2022). https://www.nature.com/articles/s41378-022-00451-6", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|51|Claude|2", "source": "prb", "split": "test", "paper_id": "prb51", "comment": "The paper claims that platelet-inspired nanoparticles (PIN) \"reseal the compromised BBB\" and promote hemostasis, but the sole evidence for this claim is reduced IgG staining—an indirect and non-specific marker that cannot distinguish between BBB structural repair and reduced inflammation-induced permeability. No direct markers of BBB structural integrity (e.g., tight junction proteins) were assessed.\n\n\"BBB permeability was evaluated by staining immunoglobulin G (IgG) to assess the potential resealing function of SPPINDEX and PIN groups. IgG is a classic biomarker for BBB leakage, as it is a blood serum protein and not commonly found in the brain parenchyma.\"\nWhile IgG extravasation can indicate BBB dysfunction, it is an indirect and non-specific measure. IgG leakage can result from multiple mechanisms including inflammation-induced permeability changes that do not reflect structural BBB damage or repair. The claim of \"BBB resealing\" implies structural restoration, but IgG staining alone cannot distinguish between reduced inflammation (which could independently decrease IgG extravasation) and actual repair of the BBB's physical barrier components.\n\"The significantly reduced IgG levels in both the SPPINDEX and PIN groups suggest that the nanoparticles may facilitate blood-brain barrier (BBB) resealing and promote hemostasis at sites of IME insertion-induced microhemorrhage.\"\nThe authors appropriately use \"suggest\" and \"may facilitate,\" indicating these are hypotheses rather than demonstrated mechanisms. However, the conclusions and abstract present BBB resealing as an established mechanism contributing to the therapeutic effects. Without direct evidence of tight junction protein restoration (e.g., ZO-1, claudin-5, occludin staining) or ultrastructural analysis of the BBB, the claim of \"resealing\" remains speculative. The observed IgG reduction could alternatively reflect general anti-inflammatory effects rather than physical BBB repair.\n\"TJ proteins such as claudin-5, occludin, and ZO-1 are downregulated after the first few days of TBI but can be upregulated 1–2 weeks after injury when the BBB regains functional integrity.\" [[2]](#citation-list)\nThe neuroscience literature establishes that tight junction (TJ) proteins such as claudin-5, occludin, and ZO-1 are the gold-standard markers for assessing BBB structural integrity and repair. These proteins form the physical barrier of the BBB, and their assessment is necessary to demonstrate actual BBB resealing. The paper under review does not include any TJ protein analysis, making the claim of BBB resealing mechanistically unsupported. Standard practice in BBB research would include immunohistochemical staining for these TJ proteins to substantiate claims of BBB repair.\n\nReferences:\n[2] Sweeney, M.D., Zhao, Z., Montagne, A., Nelson, A.R. & Bhosle, R. \"Structure, Function, and Regulation of the Blood-Brain Barrier Tight Junction in Central Nervous System Disorders.\" *Frontiers in Physiology* 11:914 (2020). https://www.frontiersin.org/journals/physiology/articles/10.3389/fphys.2020.00914/full", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|51|Claude|3", "source": "prb", "split": "test", "paper_id": "prb51", "comment": "The study employs intra-arterial (carotid artery) administration via surgically implanted vascular catheters—a route that the authors acknowledge has \"limited\" clinical translatability due to \"unexpected risks, vascular and neural toxicity\"—yet the paper presents the therapeutic efficacy as broadly applicable. This administration route limitation fundamentally undermines the clinical relevance of the demonstrated effects.\n\n\"The clinical translatability of intra-arterial administration is limited due to its unexpected risks, vascular and neural toxicity [88], particularly with repeated weekly dosing. The initial intention to use intra-arterial injection with pre-implanted catheters in this study was to avoid complications such as phlebitis from weekly tail vein injections, which could affect the quality of drug delivery.\"\nThe authors acknowledge that intra-arterial administration has significant limitations for clinical translation, including risks of vascular and neural toxicity. This is a fundamental methodological concern because the therapeutic effects demonstrated may not be reproducible via clinically feasible routes. Intra-arterial drug delivery can achieve substantially different tissue concentrations and biodistribution compared to intravenous administration, meaning the observed therapeutic benefits may not translate to clinically practical delivery methods.\n\"Future studies will focus on optimizing SPPINDEX dosing by reducing the treatment duration from 8 weeks of weekly administration to 4 weeks while evaluating whether the recording performance can be sustained up to 8 weeks and even 16 weeks, using a larger animal model such as rabbits via intravenous injection.\"\nThis future direction explicitly acknowledges the need to validate results via intravenous injection, implicitly confirming that the current intra-arterial approach is not clinically practical. However, the abstract and conclusion of the paper do not adequately communicate this limitation, presenting the treatment as a promising therapeutic strategy without clearly qualifying that it has not been validated using a clinically feasible administration route.\n\"In comparison to intravenous delivery, intra-arterial administration increases intra-tumor drug concentration and accelerates systemic clearance... However, severe vascular toxicity and neurotoxicity have been reported in several clinical studies.\" [[3]](#citation-list)\nThe neurosurgery and drug delivery literature documents that intra-arterial administration achieves substantially different pharmacokinetics compared to intravenous delivery, with higher local concentrations but also significant safety risks. The paper's demonstration of efficacy via intra-arterial delivery cannot be assumed to translate to intravenous administration, which would be required for practical clinical application. This represents a significant gap between the experimental design and the paper's broader implications for clinical utility.\n\nReferences:\n[3] Vogelbaum, M.A. & Bhardwaj, R.D. \"Strategies for Improved Intra-arterial Treatments Targeting Brain Tumors: a Systematic Review.\" *Frontiers in Oncology* 10:1443 (2020). https://www.frontiersin.org/journals/oncology/articles/10.3389/fonc.2020.01443/full", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|51|Claude|4", "source": "prb", "split": "test", "paper_id": "prb51", "comment": "The Methods section contains a clear error in sample size reporting where \"W1-4 SPPINDEX\" is listed twice with different values, indicating either a transcription error or inconsistent data handling that compromises reproducibility and reader confidence in the reported results.\n\n\"For Vpp, noise, SNR, spike rate, and units per active channel data, the sample size (N) represents the total number of active channels for different treatment groups at different phases: 93 for W1-4 SPPINDEX, 51 for W1-4 SPPINDEX, 77 for W1-4 PIN, 43 for W5-8 PIN, 81 for W1-4 TH, 38 for W5-8 TH, 86 for W1-4 Free DEXSP, 30 for W5-8 Free DEXSP.\"\nThe sample size list reports \"93 for W1-4 SPPINDEX, 51 for W1-4 SPPINDEX\"—the same time phase (W1-4) is listed twice for the SPPINDEX group with different values (93 and 51). One of these values should logically be \"W5-8 SPPINDEX\" based on the pattern used for other treatment groups. This error creates ambiguity about the actual sample sizes used for statistical analyses. If the correct value for W5-8 SPPINDEX is 51 (suggesting substantial electrode dropout by the later phase), this would be consistent with the other groups but is not clearly stated. If both phases truly had different active channel counts that were both labeled as W1-4, this represents a more fundamental data handling error. This error undermines the reader's ability to assess the statistical validity of the reported findings and reproducibility of the study.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|51|Claude|5", "source": "prb", "split": "test", "paper_id": "prb51", "comment": "The immunohistochemical analyses were performed only at the 8-week endpoint, yet the paper draws mechanistic conclusions about how reduced neuroinflammation causes improved recording performance over time. This single-timepoint histological assessment cannot establish the temporal relationship between tissue changes and the week-by-week recording improvements claimed.\n\n\"Immunohistochemistry (IHC) staining was performed on brain slices to visualize and assess neuron loss, microglial activation, astrocyte activation, and blood-brain barrier (BBB) permeability (antibodies listed in Table S1).\"\nThe Methods section describes IHC performed on endpoint tissue only. While the paper reports weekly electrophysiological recording data spanning 8 weeks (Figure 3), all histological data comes from a single 8-week endpoint. This experimental design cannot establish whether the histological improvements observed at 8 weeks (higher neuron density, lower activated microglia, etc.) were present during the earlier weeks when recording improvements were also observed, or whether the tissue changes preceded, coincided with, or followed the electrophysiological improvements.\n\"This increase in neuron density likely contributes to the improved recording performance observed with SPPINDEX treatment.\"\nThis causal interpretation linking increased neuron density to improved recording performance assumes that the tissue state at 8 weeks reflects the tissue state at earlier timepoints when recording improvements were observed. However, without histological data from intermediate timepoints (e.g., weeks 2, 4, 6), this causal relationship remains speculative. The tissue environment at 8 weeks may differ substantially from earlier phases, and the observed histological improvements may represent late-stage changes that do not explain the early recording benefits. Multiple timepoint histological analysis is standard practice in longitudinal neural implant studies when making mechanistic claims about temporal relationships.\n\"To evaluate the therapeutic effects of SPPINDEX on neuronal health and viability around the insertion site, brain tissues from all groups were stained with NeuN at the 8-week endpoint.\"\nThe paper explicitly states that brain tissue was analyzed at the \"8-week endpoint\" only. While this design choice reduces the number of animals required, it limits the conclusions that can be drawn about how tissue changes relate to the temporal pattern of recording improvements. The paper shows that recording performance declined over time in all groups (though less in SPPINDEX), but the single-timepoint histology cannot reveal whether tissue deterioration correlated with recording deterioration at intermediate timepoints.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|51|GPT|1", "source": "prb", "split": "test", "paper_id": "prb51", "comment": "This paper’s statistical testing for electrophysiology outcomes (AEY, units/channel, and exported unit metrics) is likely invalid because the analysis treats electrode channels (and derived per-channel/unit quantities) as independent samples despite being nested within animals and repeatedly observed over time.\n\n“True positive signal units were manually verified following previously established protocols [58]. The active electrode yield in each treatment group for each week was calculated by dividing the total number of active channels (defined as those with at least one active unit) by the total number of channels (16 channels per IMEs device × number of animals for each treatment in the specific week, excluding channels that never have any active units). The proportion of active channels for each treatment group in each time phase (the first four weeks, W1-4, and the last four weeks, W5-8) was calculated similarly, but by summing the total active and total channels across all weeks in the respective time phase. On a weekly basis, the total number of channels (N) was as follows: 107 for SPPINDEX, 104 for PIN, 104 for TH, and 118 for Free DEXSP.”\nThe manuscript explicitly defines the effective sample size for weekly AEY comparisons as a count of channels, not a count of animals, and then applies inferential statistics to those channel-level totals. Channels within the same implanted array share the same animal, surgery, device, and recording session, so they are not statistically independent replicates of the treatment. This creates classic pseudoreplication: the apparent “N” is inflated relative to the true number of experimental units (animals), shrinking standard errors and making week-by-week differences look more significant than they are. The problem is compounded by repeated measurements across weeks (the same animals and many of the same channels are observed repeatedly), which further violates independence assumptions underlying simple proportion tests. As a result, reported p-values and “significant” week-by-week differences are not reliable evidence that the treatment truly improves recording performance at the animal level. A more defensible approach would model AEY with animal as the experimental unit (e.g., mixed-effects logistic/Poisson models or summary measures per animal), with appropriate handling of time as a repeated factor.\n“A two-sided proportions z-test was performed using an R-based script to calculate significant statistical differences in active electrode yield between groups on a weekly basis, as well as the proportion of active electrode between and within groups at different study phases.”\nA two-sided proportions z-test assumes independent Bernoulli trials (here, implicitly, “channel is active” events) and a correctly specified effective sample size. The paper’s own methods define those trials as channel-level outcomes, yet channels are clustered within animals and arrays, and many biological and technical sources of covariance (tissue response, connector condition, anesthesia/awake transition, and headstage noise) act at the animal/session level. Ignoring clustering typically inflates Type I error rates, making “significance” easier to obtain even when the true animal-level effect is smaller or absent. Because the authors also test each week separately, the analysis additionally invites multiple-testing issues across timepoints without a clearly stated global modeling strategy. Consequently, the central claim of “significantly improved” AEY over 8 weeks rests on a statistical procedure whose assumptions are not met by the study design as described. This undermines the validity of the electrophysiology conclusions even if the underlying raw recordings are sound.\n“Pseudoreplication occurs when observations are not statistically independent, but treated as if they are. This can occur when there are multiple observations on the same subjects, when samples are nested or hierarchically organised, or when measurements are correlated in time or space.” ([1](https://pmc.ncbi.nlm.nih.gov/articles/PMC2817684/))\nThe paper’s electrophysiology design matches the situations described here: multiple channels per subject (nested data) and repeated measurements over time (correlated observations). The manuscript’s inference treats channel counts as if they were independent replicates, which is precisely the error Lazic warns can yield “meaningless results.” This matters because AEY, SNR, noise, and units/channel are all computed from channels within the same array and animal, so channel-to-channel covariance is expected rather than exceptional. The quote directly supports the concern that the study’s p-values can be substantially miscalibrated when dependencies are ignored. It also highlights that correct inference should be framed around the experimental unit (animals) or explicitly model the hierarchy, neither of which is clearly implemented for the primary AEY claim. Therefore, the manuscript’s strongest quantitative evidence is methodologically fragile.\n“These so-called 'nested designs' yield data that cannot be considered to be independent, and so violate the independency assumption of conventional statistical methods such as the t test. Ignoring this dependency results in a probability of incorrectly concluding that an effect is statistically significant that is far higher (up to 80%) than the nominal α level (usually set at 5%).” ([2](https://pubmed.ncbi.nlm.nih.gov/24671065/))\nThe electrophysiology data structure described in the manuscript is a nested design: channels (and units) are nested within an implanted device and animal, and outcomes are repeatedly assessed across time. Even though the manuscript uses a z-test (and other models) rather than a t-test in some places, the core issue is the same: conventional tests that assume independence will overstate evidence for an effect when applied to nested observations. The quote provides a field-specific warning from neuroscience statistics that the false-positive risk can become dramatically larger than the nominal α when dependency is ignored. This directly challenges the reliability of the paper’s week-by-week “significant” differences and phase comparisons based on channel counts. Because the main conclusion is anchored to statistically significant electrophysiology improvements, any inflation of significance meaningfully affects the paper’s validity and the robustness of its conclusions. At minimum, the manuscript needs a reanalysis that treats animals as the experimental units or uses multilevel models with random effects for animal (and potentially array/channel).", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|51|GPT|2", "source": "prb", "split": "test", "paper_id": "prb51", "comment": "This paper’s primary performance metric (AEY) is defined and computed in a way that conditions the denominator on the outcome (excluding channels that are never active across the study), which can systematically inflate AEY and bias between-group comparisons.\n\n“Active electrode yield (AEY), calculated to assess recording performance, was determined by conducting biweekly recordings and analyses. It was defined as the percentage of active channels (channels with detected active units) relative to the total potential channels (excluding channels without any detected active units throughout the entire study).”\nBy excluding channels “without any detected active units throughout the entire study,” the metric uses post hoc information from the entire 8-week trajectory to define the denominator at each week. This makes AEY partially self-referential: a channel’s lifetime outcome (ever active vs. never active) determines whether it counts in the denominator for every week, including early weeks. The approach inflates AEY relative to a more standard definition that uses all physical channels as potential recording sites, because permanently silent channels are removed rather than counted as failures. Critically, the exclusion can differ by treatment group if a treatment changes the probability that a channel is ever active (or if groups differ in device quality, surgical microdamage, or connector failures), introducing differential denominator shrinkage that itself amplifies apparent group differences. This definition also reduces interpretability for translational readers: a clinician cares about the fraction of all implanted channels that provide usable units at a given time, not only the fraction of channels that will eventually succeed at least once. Because AEY is the central endpoint supporting “improved recording performance,” this outcome-dependent definition threatens the robustness of the conclusion.\n“The active electrode yield in each treatment group for each week was calculated by dividing the total number of active channels (defined as those with at least one active unit) by the total number of channels (16 channels per IMEs device × number of animals for each treatment in the specific week, excluding channels that never have any active units).”\nThe methods section reiterates that “total number of channels” is not the physical 16×animals channel count, but that count minus channels that never become active. This means the paper does not report AEY on the natural, fixed scale of the device (0–16 per array) but on a filtered scale that depends on observed outcomes. Using such a filtered denominator can produce higher percentages without any true improvement in the number of usable channels, simply by reclassifying failures as “non-potential” and removing them. The filtering is especially problematic when reporting week-specific AEY trajectories, because it can make early-week AEY appear better even if the excluded channels would have been silent early on (which is precisely what “never active” implies). In comparative studies, it is standard to keep denominators fixed to avoid precisely this kind of bias; otherwise, performance metrics can be tuned by exclusion rules rather than by the intervention’s true effect. The manuscript does not provide sensitivity analyses showing whether conclusions hold under a fixed-denominator AEY definition (all 16 channels per array per animal). Without that, the headline AEY improvement is difficult to interpret as an objective performance gain.\n“Animals were separated to four cohorts based on the treatments: drug-loaded nanoparticles (SPPINDEX, n = 7), unloaded nanoparticles (PIN, n = 7), free drug (Free DEXSP, n = 8) and diluent control (TH, n = 7).”\nThe cohort sizes imply fixed physical channel counts per week of 112 channels for groups with n=7 and 128 channels for the group with n=8, before any exclusions. Yet the paper later reports weekly “total number of channels (N)” values (e.g., 107, 104, 118) that are smaller than these physical totals, demonstrating that denominator filtering is actively changing the scale on which AEY is computed. Because the number of excluded channels differs across groups (e.g., the n=8 group can exclude more channels), the AEY percentages are not strictly comparable across treatments unless the exclusion mechanism is shown to be treatment-invariant. This is not a minor reporting nuance: a few percentage points can alter “significance” and effect sizes when week-by-week curves are compared. Moreover, excluding permanently silent channels removes an important dimension of chronic implant performance—complete site failure—that many IME studies explicitly aim to reduce. The manuscript should present AEY (or an additional endpoint) on a fixed denominator to quantify absolute functional yield.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|51|GPT|3", "source": "prb", "split": "test", "paper_id": "prb51", "comment": "The histology analyses (distance-binned NeuN counts and GFAP/CD68/IgG intensity profiles) are statistically and methodologically under-specified for reliable inference because they analyze many distance bins separately and likely include nested subsamples (multiple slices per implant/animal), risking pseudoreplication and uncontrolled multiple comparisons.\n\n“For each IME implant hole, at least three different brain slice depths were analyzed for both the SECOND fluorescent intensity analysis and the Cellpose neuron density analysis. For each treatment group, brain tissues from a minimum of four animals were included in both analyses.”\nThis description indicates multiple measurements per implant hole (≥3 slice depths), and potentially multiple implant holes per animal (the study implants both functional and non-functional devices in the same rat). Such a sampling scheme creates nested data: slices within holes, holes within animals, and multiple distance bins within each slice. The manuscript does not clearly state whether it averages these subsamples to one value per animal (or per implant) before statistical testing, or whether subsamples contribute multiple independent datapoints. If subsamples are treated as independent in ANOVA, the analysis will inflate the effective sample size, underestimate variability, and increase false positives—especially in distance-profile data where adjacent bins are spatially correlated. Even if averaging was performed, the paper should specify the aggregation strategy and the experimental unit for each test to allow readers to assess independence. With “a minimum of four animals” per group, the study is particularly sensitive to analytical choices that inadvertently multiply N. Because the paper’s mechanistic interpretation depends on bin-level “significant” reductions near the interface, mis-specified experimental units can directly distort the biological conclusions.\n“A one-way ANOVA with post hoc Tukey pair-wise test in GraphPad was used to compare normalized neuron density (NeuN) and normalized fluorescence intensity for astrocyte (GFAP), activated microglia/macrophage (CD68), and Immunoglobulin G (IgG) among treatment groups within each distance interval.”\nTesting “within each distance interval” implies many separate hypothesis tests (one per 50 µm bin) for each marker, in addition to multiple treatment comparisons within each bin. While Tukey controls the family-wise error rate among pairwise comparisons inside a single bin, it does not control the experiment-wise error across the many bins tested along the distance axis. This makes it easy to obtain some “significant” bins by chance, particularly when adjacent bins are correlated and when normalized values are constrained by construction. A common practice for such radial profiles is to fit a hierarchical model or repeated-measures/mixed model with distance as a within-sample factor, which both respects correlation structure and provides a single, interpretable test of group-by-distance effects. The manuscript’s approach also risks selectively emphasizing the closest bins (0–50, 50–100 µm) where the narrative is strongest, without a clearly defined multiplicity-control plan. Because the histology results are used to support mechanistic claims about BBB permeability and inflammation, uncontrolled multiple testing can materially weaken the evidentiary basis. At minimum, the paper should report a global analysis plan for distance profiles (and corrected inferences) rather than bin-by-bin ANOVAs.\n“Non-functional IMEs were manually implanted at approximately 2 mm depth for improving the sample size (N) for histology study.”\nThe study explicitly increases histology N by adding a second, non-functional implant per animal and implanting it manually, while the functional IME is inserted with a stereotaxic frame. Manual implantation can change insertion trajectory, speed, and microvascular damage, all of which are known to influence acute hemorrhage, BBB disruption, and chronic gliosis near neural implants. If histology samples include these non-functional implant sites, the analysis mixes two implantation modalities, potentially introducing systematic variance unrelated to treatment and complicating interpretation of “implant-interface” biology. If histology instead uses only one implant type, the manuscript should state this clearly; otherwise readers cannot determine whether the histology corresponds to the same devices used for electrophysiology outcomes. Moreover, using two implant holes per animal creates within-animal correlation that should be modeled (or averaged per animal) rather than treated as independent replicates. Because the paper’s central argument links improved AEY to improved tissue response, any ambiguity in which implant sites contribute to histology is a major methodological weakness. Clarifying the unit of analysis and implant selection is necessary to support the claimed mechanistic pathway.\n“Conflating experimental units with subsamples or repeated measurements can lead to artificial inflation of the sample size. For example, measurements from 50 individual cells from a single mouse represent *n* = 1 when the experimental unit is the mouse.” ([5](https://journals.plos.org/plosbiology/article?id=10.1371/journal.pbio.3000411))\nThe manuscript’s histology workflow (multiple slices per implant and many bins per slice) creates precisely the risk described here: many subsamples can be mistaken for independent replicates if the experimental unit is not stated and enforced in the analysis. In distance-binned immunofluorescence, each bin mean is a subsample derived from the same tissue section and implant site, so bin-level tests can dramatically overcount information if treated as independent. The quote also highlights that artificial N inflation can “invalidate the analysis and resulting conclusions,” which is especially pertinent when the paper uses bin-wise significance to argue for reduced inflammation and BBB leakage near the interface. Because the manuscript only states “a minimum of four animals” per group, the temptation to rely on subsample-based N for statistical power is strong, making explicit reporting and correct modeling essential. This external guideline frames the issue as a validity threat rather than a stylistic preference. Therefore, without a clearly specified experimental unit and multiplicity-aware modeling, the histology significance claims are not robust.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|51|GPT|4", "source": "prb", "split": "test", "paper_id": "prb51", "comment": "The paper overstates mechanistic conclusions that SPPINDEX “reseals” the BBB and “achieves targeted delivery” of dexamethasone to the implant interface, because the presented data do not directly measure BBB repair dynamics, nanoparticle localization at the implant site, or local dexamethasone exposure.\n\n“BBB permeability was evaluated by staining immunoglobulin G (IgG) to assess the potential resealing function of SPPINDEX and PIN groups. IgG is a classic biomarker for BBB leakage, as it is a blood serum protein and not commonly found in the brain parenchyma. In the SPPINDEX group, IgG intensity was significantly reduced up to 550 µm from the implant site in comparison to the TH group (Fig. 5 E, significant levels after 200 µm shown in Table S5). Similarly, animals treated with PIN also had significantly lower IgG intensity starting from 50 µm up to 600 µm from the implant site compared to the TH group (Table S5). The significantly reduced IgG levels in both the SPPINDEX and PIN groups suggest that the nanoparticles may facilitate blood-brain barrier (BBB) resealing and promote hemostasis at sites of IME insertion-induced microhemorrhage.”\nIgG staining at an 8-week endpoint can indicate differences in chronic extravasation of serum proteins, but it does not by itself establish that BBB “resealing” occurred, nor when it occurred relative to implantation. The manuscript’s own framing emphasizes an “initial” prevention of blood-derived trigger invasion, yet the presented BBB proxy is measured only at the terminal timepoint, after weeks of repeated dosing and evolving tissue response. Lower IgG at 8 weeks could arise from many pathways (e.g., reduced chronic inflammation, altered vascular remodeling, or differences in glial scar permeability), and it is not a direct readout of early hemostasis or acute microhemorrhage control. Moreover, both PIN and SPPINDEX show reduced IgG, which weakens the specificity of attributing benefits to dexamethasone targeting versus nanoparticle vehicle effects. Because the mechanism is central to the paper’s narrative and to the rationale for systemic dosing, the evidence as presented is insufficiently specific to justify strong mechanistic language. A stronger case would require time-resolved BBB permeability assays (e.g., acute tracer leakage, Evans blue/fluorescent dextran at early timepoints) and/or direct measures of microhemorrhage/hemostasis.\n“The significant improvement in active electrode yield observed in the PIN-only group compared to the TH and Free DEXSP groups validates that the nanoparticle itself, even without drug loading, can enhance recording performance by resealing the compromised BBB and inhibiting the influx of blood-derived proteins, as seen in histological analysis.”\nThis sentence claims that the electrophysiology improvement “validates” BBB resealing as the causal driver, but the paper does not present direct evidence linking BBB status changes to AEY changes at the same animals and timepoints. The only BBB-related evidence described is terminal IgG staining, which is correlative and does not establish directionality or temporal precedence. In addition, the manuscript’s own electrophysiology analyses use channel-level N and outcome-conditioned denominators, making the asserted “validation” especially vulnerable to analytical artifacts. The claim also conflates two distinct concepts: limiting influx of blood-derived proteins and “resealing” ruptured BBB, which requires direct vascular integrity measurements. Without a causal design (e.g., mediational analysis at animal level with repeated BBB assays, or interventions that selectively alter hemostasis without anti-inflammatory drug), “validates” is too strong. As written, the statement risks presenting an attractive mechanism as if it were established, when the data support only an association between treatment and lower IgG at endpoint.\n“The poorer recording performance in the Free DEXSP group suggests the importance of targeted drug delivery. This study demonstrates that targeted delivery using PIN was successfully achieved.”\nThe manuscript does not show a direct measurement of drug targeting, such as nanoparticle accumulation at the implant site, local dexamethasone concentration near the interface, or reduced systemic exposure relative to free drug at matched dose. “Free DEXSP performs worse than TH” is not evidence that targeting occurred; it only indicates that non-targeted systemic dexamethasone at the chosen regimen did not help in this model and might have harmed. Many alternative explanations remain consistent with the data, including pharmacokinetic differences, dosing timing, or systemic side effects affecting neural activity and behavior. A claim that “targeted delivery using PIN was successfully achieved” typically requires biodistribution/target engagement evidence within the same study, especially when the therapeutic argument depends on local delivery at an implant interface. The paper’s own later language (“potentially released”) underscores that local delivery was inferred rather than demonstrated. Therefore, the mechanistic conclusion overreaches beyond the evidence presented.\n“For the SPPINDEX treatment, in addition to initially disrupting self-perpetuating neuroinflammation by reducing the invasion of foreign substances into the brain parenchyma, dexamethasone sodium phosphate (DEXSP) was potentially released into the brain parenchyma and absorbed by activated microglia near the implant site via the injury-targeted delivery platform (PIN).”\nThe explicit use of “potentially” acknowledges the lack of direct measurement of dexamethasone release, brain penetration, and microglial uptake in this experiment. This is a major gap because dexamethasone sodium phosphate is hydrophilic and its transport, conversion, and local concentration at an intracortical implant interface depend on complex vascular and tissue barriers. Without measuring DEXSP (or dexamethasone) levels in brain tissue near the implant, the proposed microglial glucocorticoid receptor mechanism remains speculative. Speculation is acceptable in discussion, but the paper’s conclusion section subsequently presents targeted delivery and BBB resealing as likely drivers of improved recording performance, which elevates hypothesis to inference. This matters for translation: the therapy’s value proposition hinges on combining hemostasis and targeted anti-inflammatory exposure. A more conservative interpretation would separate observed outcomes (AEY and histology differences) from unverified mechanistic steps.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|51|GPT|5", "source": "prb", "split": "test", "paper_id": "prb51", "comment": "The paper’s main quantitative claims are not fully reproducible because it relies on custom R scripts and MATLAB software for electrophysiology processing and statistical testing that are not provided in the accompanying code/data materials, and the provided electrophysiology data documentation is insufficient.\n\n“Custom R scripts were used to rearrange in vivo extracellular single-unit recording raw data, including the number of units and active channel yield across different animals, treatments, and weeks.”\nThe manuscript indicates that custom R scripts are central to computing and organizing the electrophysiology endpoints, including the primary AEY outcome. Yet the accompanying code materials (as provided here) do not include these R scripts, preventing independent verification of how channels were excluded, how week-by-week denominators were constructed, and how counts were aggregated across animals and time. This is not a minor implementation detail: the AEY definition and the channel-level N choices materially affect effect sizes and p-values. Without the actual scripts (and their input formats), readers cannot reproduce the reported trajectories or check for edge cases such as missing sessions, dead channels, or device failures. Moreover, reproducibility concerns interact with the statistical-validity issues: when analyses are non-standard (e.g., channel-based proportion tests), code transparency is especially important to assess correctness. The absence of the scripts therefore undermines confidence in the electrophysiology results as implemented.\n“Calculated recording parameters were obtained using custom-developed MATLAB software (Mathworks, Natick, MA).”\nThe exported metrics (Vpp, noise, SNR, spike rate, and units/channel) are derived from a custom MATLAB pipeline, but that pipeline is not included in the provided repository. These metrics are used to support claims about signal quality (e.g., noise and SNR differences) and are part of the paper’s multi-metric interpretation of recording performance. Without the MATLAB code, it is not possible to verify key implementation choices such as filtering, referencing, spike exclusion, and outlier handling (e.g., ROUT with Q=5%), all of which can meaningfully change distributions. Reproducing these metrics from raw recordings would require many implicit parameters and decisions that are only partially described in text. In electrophysiology, small methodological differences can change which units are detected and how SNR is computed, so code availability is a standard expectation for robust reproducibility. The lack of this code limits the manuscript’s transparency and the community’s ability to build upon the work.\n“This repository contains analysis code for processing histological images to quantify neuron density at various distances from implanted devices.”\nThe provided code README frames the repository as primarily supporting histology image processing, not the electrophysiology analyses that drive the headline claims. While histology code availability is valuable, it does not address reproducibility of the primary endpoint (AEY over time) or of the spike-sorting and metric extraction steps. This mismatch between what the paper reports as “custom scripts/software” and what is actually packaged for readers creates a partial reproducibility story: one component is supported, but the core electrophysiology pipeline is not. Because the study’s main novelty claim centers on improving recording performance, omitting the recording-analysis code is a substantial barrier to independent validation. At minimum, readers need the scripts that compute AEY and per-channel metrics from exported sorter outputs, along with a clear specification of inputs/outputs. Without that, the work is difficult to audit or extend.\n“# Placeholder text”\nThe electrophysiology data folder’s readme is a placeholder, providing no guidance on what the included spreadsheets represent (animal-level vs. channel-level), how missing data were handled, or how figures map to source files. In practice, this forces readers to guess the meaning of columns, row units, and preprocessing steps, which is precisely what good reproducibility packaging is meant to avoid. This is particularly problematic because the paper’s methods define sample sizes in terms of active channels and uses exclusions and outlier removal; without clear data provenance, it is hard to reconstruct the analysis unit. When repositories include only derived spreadsheets, documentation becomes essential for traceability back to raw recordings and for checking assumptions. A placeholder readme signals that the data release is incomplete for reproducibility purposes. Given the statistical complexity and the centrality of electrophysiology outcomes, this documentation gap is significant.\n“ARRIVE Essential 10 These ten items are the basic minimum that must be included in any manuscript describing animal research. Without this information readers and reviewers cannot assess the reliability of the findings.” ([4](https://arriveguidelines.org/arrive-guidelines))\nWhile ARRIVE primarily targets animal-study reporting, its core message—minimum information needed to assess reliability—also applies to computational reproducibility of derived outcomes. Here, key computational steps (custom R and MATLAB analyses) are essential to evaluate whether the reported findings are reliable, yet are not made available in the accompanying materials. This prevents reviewers and readers from checking that statistical tests match the intended experimental units and that exclusions and outlier handling were implemented as described. In modern biomedical engineering practice, sharing analysis code is a common mechanism to meet the transparency goals embodied by ARRIVE-like standards. The quote underscores that missing methodological detail is not merely inconvenient; it blocks reliability assessment. Therefore, the manuscript’s current code/data release falls short of reproducibility expectations for a results-driven electrophysiology study.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|51|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb51", "comment": "The paper claims that SPPINDEX treatment improves intracortical microelectrode recording performance, but the results show significantly lower signal-to-noise ratio (SNR) and higher noise compared to the control group, which contradicts the claim of overall improvement.\n\n\"Although the signal-to-noise ratio (SNR) was significantly lower in the SPPINDEX group compared to the TH group (p < 0.001 in W1_4, p < 0.0001 in W5_8) for both phases of the study, the mean SNR remained above 5 for all treatments, demonstrating high-quality recordings across all groups\"\nThe authors dismiss the statistically significant reduction in SNR (p < 0.0001) by stating it remained above a threshold. However, a treatment that increases the number of active channels (yield) while significantly degrading the signal quality (SNR) of those channels represents a trade-off rather than a clear improvement. The lower SNR suggests that while more units are detected, the recording quality of individual units is compromised, potentially due to the higher noise levels observed.\n\"Noise levels in the SPPINDEX group were significantly higher compared to the TH and Free DEXSP groups (p < 0.05 to TH, p < 0.001 to Free DEXSP) during the first four weeks, indicating a potential increase in noise associated with SPPINDEX treatment during the early weeks\"\nThe increased noise levels in the treatment group directly contribute to the lower SNR. This finding raises concerns about whether the nanoparticles or the drug release mechanism might be introducing electrical noise or altering the tissue impedance in a way that detrimentally affects signal quality, a critical aspect of neural recording that is not adequately addressed.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|51|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb51", "comment": "The paper claims that the platelet-inspired nanoparticles (PIN) achieve targeted delivery and accumulation at the implant site, but it fails to provide direct experimental evidence (such as biodistribution studies or in vivo imaging) to support this mechanism in the manuscript.\n\n\"This study demonstrates that targeted delivery using PIN was successfully achieved.\"\nThis statement is unsupported by direct evidence in the manuscript. The authors rely on downstream functional outcomes, such as reduced IgG leakage, to infer targeted delivery. However, reduced IgG leakage only indicates BBB repair or hemostasis, not necessarily that the nanoparticles themselves accumulated at the site to deliver the drug locally.\n\"Significantly lower IgG levels around the implant sites were observed in the SPPINDEX group, suggesting that the improved recording performance may be due to reduced infiltration of blood-derived substances into the brain parenchyma.\"\nWhile IgG reduction is a positive outcome, it is indirect evidence. To claim \"targeted delivery,\" the authors should have demonstrated the physical presence of the nanoparticles at the electrode interface using methods like IVIS imaging or fluorescent histology. Notably, the provided code repository contains a folder named `Li 2025 Biomaterials/DATA/IVIS`, suggesting that such data may exist but was omitted from the manuscript, which is a significant oversight for a paper centered on a targeted delivery system.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|51|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb51", "comment": "The \"Free DEXSP\" (systemic free drug) control group performed significantly worse than the vehicle control (TH), raising concerns about the systemic toxicity of the drug or the experimental design, which are not adequately explained.\n\n\"Surprisingly, the Free DEXSP group exhibited significantly worse recording performance compared to the negative control (TH group), consistent with findings from previous studies on the long-term therapeutic efficacy of systemic DEX administration\"\nThe fact that the free drug treatment resulted in worse outcomes than the negative control (saline/trehalose) suggests a detrimental effect of systemic dexamethasone at the used dosage. If the drug itself is toxic or harmful to recording performance when given systemically, the improved performance of SPPINDEX might be attributed to the encapsulation preventing systemic exposure rather than the targeted delivery mechanism.\n\"Weights in the animals were significantly reduced in Free DEXSP group compared to the TH at week 4 and week 8, suggestion temporary effects on metabolism of animals from weekly repeated Free DEXSP treatment.\"\nThe significant weight loss confirms systemic toxicity. The authors attempt to explain the poor recording performance by citing a study on sepsis [83], which is a different pathological context. A more rigorous control would have been a lower dose of free DEXSP or a comparison with local delivery to isolate the effect of the delivery system from the drug's toxicity.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|51|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb51", "comment": "The paper compares the systemic nanoparticle treatment primarily with systemic free drug administration, but fails to compare it with local delivery methods (e.g., drug-coated electrodes), which are a common and effective strategy for improving neural recording performance.\n\n\"Zhong et al. explored local delivery of DEX by coating microelectrodes with DEX-encapsulated nitrocellulose prior to insertion... Although this approach significantly reduced neuroinflammation and improved signal recording quality, it was limited by a single administration and depletion of the drug\"\nThe authors acknowledge that local delivery is effective but dismiss it based on the limitation of single administration. However, to demonstrate the superiority or clinical relevance of their systemic approach, they should have compared SPPINDEX with a DEX-coated electrode group. This would establish whether the systemic \"targeted\" delivery offers any advantage over the simpler, site-specific local delivery that avoids systemic exposure entirely.\n\"Gaire et al have demonstrated that systemic administration of dexamethasone (DEX) acutely post IMEs insertion may not improve the recording functionality of IMEs, even though it attenuated neuroinflammation\" [38]\nSince systemic administration is known to be problematic (as cited), the relevant benchmark for a new therapy is not the failed systemic approach, but the successful local approach. By only comparing to a \"strawman\" (systemic free DEX) that performs worse than control, the paper inflates the perceived benefit of the nanoparticle treatment.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|51|Gemini|5", "source": "prb", "split": "test", "paper_id": "prb51", "comment": "The paper states that custom software was used for electrophysiological analysis, but this code is not included in the provided repository, hindering reproducibility.\n\n\"Calculated recording parameters were obtained using custom-developed MATLAB software (Mathworks, Natick, MA).\"\nThe provided code repository contains Python code for histology analysis (Cellpose) but lacks the MATLAB scripts mentioned for processing the neural recording data (spike sorting, SNR calculation, etc.). Given the controversial finding regarding SNR (Item 1), access to the analysis code is crucial to verify how signal and noise were defined and calculated.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|51|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb51", "comment": "The authors added rigor to the study by examining side effects of SPPINDEX in rats up to the longest time point in the study (8 weeks post-implant). Please comment on any potential side effects and/or other safety concerns of SPPINDEX systemic administration in more chronic administration beyond 8 weeks. Also, would any difference in side effects of SPPINDEX systemic administration be expected humans vs. rats? For example, could blood clots formed outside of the injury site increase risk of heart attack or stroke? Have the authors explored other modes of delivery more local to the insertion site to circumvent concerns due to systemic delivery?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|51|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb51", "comment": "Include more details on the following methods to ensure other groups can replicate the results. In “electrophysiological analysis”: Provide more details on the ROUT method. In “IHC, Imaging and Analysis”: SECOND not defined", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|51|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb51", "comment": "The fact that free DEX worsened recording performance was an interesting result that highlights the importance of the BBB repair aspect of SPPINDEX. Were there any specific indicators from the brain tissue of the free DEX group that suggest delayed wound healing (consistent with the findings of Chen et al. as mentioned in the Discussion section)?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|51|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb51", "comment": "BBB is repeatedly defined", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|51|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb51", "comment": "Fix reference 46", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|51|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb51", "comment": "Figure 1: Not clear that neural recordings continue during weeks 2-7 from figure alone, though methods spell this out.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|51|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb51", "comment": "[Figures] Several figures are not referred to in the main text, making it unclear how they support the study’s claims. Every figure should be explicitly mentioned and discussed within the appropriate section.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|51|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb51", "comment": "[Figures] The order of figures is inconsistent, with some figures missing in the text and others appearing out of sequence. This should be carefully reviewed and corrected to improve readability.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|51|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb51", "comment": "[Figures] Figure 3D appears to be identical to Figure 3F-I, with only a different version of the graphs (different grouping but based on the same dataset). If this is the case, the authors should clarify why both are included and whether one can be removed or merged for simplicity.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|51|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb51", "comment": "[Statistical Analysis] The manuscript does not consistently indicate the number of animals (n) used in each experimental group. The sample size for each experiment should be clearly stated in figure legends.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|51|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb51", "comment": "[Results] The study presents neuron density as an indicator of SPPINDEX’s therapeutic effect (Figure 5). However, increased neuron density alone may not be a definitive marker to claim a ‘therapeutic’ effect of SPPINDEX. I suggest revising the wording to simply state it as the ‘effect of SPPINDEX’ rather than implying a therapeutic impact without additional functional validation.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|51|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb51", "comment": "[Results] SPPINDEX was administered weekly for 8 weeks. However, it’s unclear whether continuous dosing is necessary for sustained improvements in IME recording performance or if a gradual reduction in dosing could still provide long-term benefits while minimizing potential side effects.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|51|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb51", "comment": "[Results] The role of hemostatic properties in BBB sealing should be expanded upon. Is there direct evidence that PIN promotes endothelial repair?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|51|Human_2|10", "source": "prb", "split": "test", "paper_id": "prb51", "comment": "[Discussions] The initial portion of the Discussion repeats content that was already covered in the Introduction. This redundancy reduces the impact of the discussion and makes the manuscript unnecessarily lengthy.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Claude|2", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "The in vivo therapeutic efficacy assessment uses only n=3 rabbits per treatment group, which is insufficient for robust statistical analysis and limits the reliability of conclusions about the therapeutic effects of the smart contact lens compared to eye drops.\n\n\"The glaucoma induced rabbits and normal rabbits were divided into 3 groups to assess the therapeutic effects of smart contact lens and eye drop: Glaucoma induced by MC or α-chymotrypsin with eye drop (n = 3, group 1), glaucoma induced by MC or α-chymotrypsin with smart contact lens (n = 3, group 2), and the normal rabbits as a control (n = 3, group 3).\"\nUsing only three animals per group provides extremely limited statistical power to detect meaningful therapeutic differences. With such small sample sizes, the study is highly susceptible to type II errors (failing to detect real differences) and may not adequately account for inter-animal variability. Standard practice in preclinical studies typically requires larger sample sizes for therapeutic efficacy assessment, with many guidelines suggesting a minimum of 6-10 animals per group for adequate statistical power [[2]](#ref2).\n\"One-sided statistical analyses were performed by using a one-way analysis of variance (ANOVA).\"\nThe use of one-sided tests with such small sample sizes is particularly problematic. One-sided tests are generally discouraged unless there is strong prior justification, as they can inflate type I error rates. Combined with n=3 per group, this analytical approach may yield statistically significant results that lack practical reliability. Furthermore, ANOVA with only 3 samples per group provides very low degrees of freedom for error estimation, making the F-test less reliable [[3]](#ref3).\n\"The IOP change by timolol released from the smart contact lens (n = 25, **P < 0.01)\"\nWhile the IOP change analysis uses n=25 measurements, these appear to be repeated measurements from a smaller number of animals rather than independent biological replicates. The figure legend states n=25 for the IOP change analysis, but the therapeutic study only included 3 animals per treatment group. This pooling of technical replicates as if they were independent samples can lead to pseudoreplication, artificially inflating the apparent statistical significance [[4]](#ref4).\n\nReferences:\n[2] Charan J. & Kantharia N.D. \"How to calculate sample size in animal studies?\" *Journal of Pharmacology & Pharmacotherapeutics* **4**, 303-306 (2013). Available at: [https://pmc.ncbi.nlm.nih.gov/articles/PMC3826013/](https://pmc.ncbi.nlm.nih.gov/articles/PMC3826013/)\n[3] Dell R.B., Holleran S. & Ramakrishnan R. \"Sample size determination\" *ILAR Journal* **43**, 207-213 (2002). Available at: [https://academic.oup.com/ilarjournal/article/43/4/207/842986](https://academic.oup.com/ilarjournal/article/43/4/207/842986)\n[4] Lazic S.E. \"The problem of pseudoreplication in neuroscientific studies: is it affecting your analysis?\" *BMC Neuroscience* **11**, 5 (2010). Available at: [https://bmcneurosci.biomedcentral.com/articles/10.1186/1471-2202-11-5](https://bmcneurosci.biomedcentral.com/articles/10.1186/1471-2202-11-5)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Claude|3", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "While the paper reports an R²=0.88 correlation between the smart contact lens and tonometer measurements, this correlation alone does not establish the sensor's ability to accurately measure absolute IOP values, a critical limitation that parallels the known shortcomings of the FDA-approved Triggerfish system.\n\n\"Correlation of IOP measured with a smart contact lens and a tonometer (n = 80, R² = 0.88).\"\nAn R²=0.88 correlation demonstrates a relationship between sensor output and tonometer readings, but correlation does not equal accuracy for absolute IOP measurement. The paper does not report the actual measurement error (e.g., mean absolute error, Bland-Altman limits of agreement beyond what's shown briefly) or demonstrate that the sensor can reliably determine specific IOP values across different individuals without per-subject calibration.\n\"Studies suggest that the Triggerfish CLS provides reproducible data, but its validity in estimating IOP remains unknown... Mottet et al compared change in GAT IOP (taken just before and after CLS wear) with change in CLS output after 24 hours of CLS wear. The group found significant differences between GAT IOP and CLS output, and concluded that the CLS cannot be used to estimate absolute IOP at this time.\" [[5]](#ref5)\nThe FDA-approved Triggerfish system, which also uses strain gauges to detect corneal changes, has been shown to have similar correlation with IOP patterns but cannot estimate absolute IOP values. This established limitation in the field raises questions about whether the current paper's sensor can overcome these fundamental challenges, particularly since the paper relies on individual calibration curves for each rabbit (as described in Supplementary Methods) rather than demonstrating universal accuracy.\n\"To obtain the standard graph of each rabbit to convert code change to IOP level, the base codes of smart contact lens were measured before wearing smart contact lens without any tension (0 mmHg, C₀). The IOP level of each rabbit was measured by tonometer (χ mmHg). Right after that, the code outputs were measured by wearing smart contact lens (χ mmHg, C).\"\nThe paper describes per-subject calibration requiring tonometer measurements to convert sensor output to IOP values. This means the smart contact lens cannot independently measure absolute IOP without conventional tonometry calibration for each individual, significantly limiting its claimed advantage over existing IOP monitoring methods for practical clinical use.\n\nReferences:\n[5] Dunbar G.E., Shen B.Y. & Aref A.A. \"The Sensimed Triggerfish contact lens sensor: efficacy, safety, and patient perspectives\" *Clinical Ophthalmology* **11**, 875-882 (2017). Available at: [https://pmc.ncbi.nlm.nih.gov/articles/PMC5428792/](https://pmc.ncbi.nlm.nih.gov/articles/PMC5428792/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Claude|4", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "The biocompatibility assessment relies primarily on short-term in vitro cell viability tests and brief in vivo rabbit studies without comprehensive long-term safety evaluation, which is essential for a contact lens intended for therapeutic use in glaucoma management.\n\n\"To assess the cell viability and biosafety of nanomaterials, fibroblast cells (NIH 3T3) at a concentration of 5.0 × 10³ cells/ml were directly seeded on the parylene C as a blank substrate, AuHNW, D-PEDOT and AgNW as a control... After cells on each film were incubated in the cell culture medium... for 3 days, the cells were stained with calcein AM and ethidium homodimer-1 (EthD-1).\"\nThe biocompatibility assessment uses fibroblast cells (NIH 3T3) rather than human corneal epithelial cells, which would be more relevant for an ocular device. Additionally, a 3-day in vitro test does not adequately assess potential long-term cytotoxic effects of the nanomaterials, particularly given that glaucoma is a chronic disease requiring long-term treatment. Comprehensive biocompatibility studies for ophthalmic devices typically include testing with relevant corneal cell lines and longer exposure periods [[6]](#ref6).\n\"Although the temperature of chip increased up to 39.3 °C, there were not any critical thermal damages on the cornea after finishing all in vivo tests.\"\nA chip temperature of 39.3°C is concerning for a device worn on the cornea, as the normal corneal surface temperature is approximately 34-35°C. Elevated temperatures above 37°C can cause corneal epithelial damage with extended exposure. The brief statement that there were no \"critical thermal damages\" lacks quantitative assessment and does not adequately address the potential for cumulative thermal stress during the repeated or prolonged use that would be required for glaucoma management [[7]](#ref7).\n\"After 24-h wear of the SCL and the commercial contact lens... To further investigate the biocompatibility of the SCL with extended use, long-term in vivo eye irritation tests were performed on rabbit eyes (n = 3). The SCL was worn on one of the rabbit's eyes for 8 hours daily over the course of 1 week.\" [[8]](#ref8)\nThis quote from a comparable smart contact lens study demonstrates the standard for biocompatibility testing, including 24-hour continuous wear and multi-week daily wear protocols. The paper under review does not clearly report such extended wear duration testing, which is essential for establishing safety for a therapeutic device intended for chronic glaucoma management requiring repeated or continuous use.\n\nReferences:\n[6] ISO 10993-5:2009 \"Biological evaluation of medical devices — Part 5: Tests for in vitro cytotoxicity\" International Organization for Standardization. Available at: [https://www.iso.org/standard/36406.html](https://www.iso.org/standard/36406.html)\n[7] Purslow C. & Wolffsohn J.S. \"Ocular surface temperature: a review\" *Eye & Contact Lens* **31**, 117-123 (2005). Available at: [https://pubmed.ncbi.nlm.nih.gov/15894878/](https://pubmed.ncbi.nlm.nih.gov/15894878/)\n[8] Keum D.H. et al. \"Frequency-encoded eye tracking smart contact lens for human-machine interaction\" *Nature Communications* **15**, 3485 (2024). Available at: [https://www.nature.com/articles/s41467-024-47851-y](https://www.nature.com/articles/s41467-024-47851-y)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|GPT|1", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "This paper’s in vivo therapeutic-efficacy experiment uses the fellow eye as a negative control despite administering timolol to the treated eye, which can systemically lower intraocular pressure (IOP) in the contralateral eye; this undermines internal validity of the therapeutic comparisons and weakens the causal interpretation of treatment effects on IOP and downstream retinal outcomes.\n\nThe therapeutic effect of timolol released from the theranostic smart contact lens was analyzed and compared with that of eye drop (0.5 % Timoptic) in glaucoma induced rabbits. The right eyes of glaucoma rabbits were treated by eye drop every day or timolol released from the smart contact lens every other day for two weeks (Supplementary Fig. 14). The left eyes of glaucoma rabbits were treated with PBS as a negative control.\nThese sentences define the core causal contrast for the therapeutic claims: right-eye timolol treatment versus left-eye PBS “negative control” within the same animal. This design implicitly assumes the left eye is pharmacologically untreated and can therefore serve as an independent counterfactual for the treated eye. For timolol, that assumption is risky because topical beta-blockers have known systemic absorption pathways (e.g., via nasal mucosa after drainage) that can affect both eyes. If the contralateral eye experiences IOP lowering due to systemic exposure, then the left-eye IOP and retinal biomarkers are no longer a true untreated baseline. As a result, estimated treatment effects can be biased in magnitude and direction, and “non-treatment” group interpretations become ambiguous. This directly impacts whether the paper’s therapeutic conclusions are valid.\nGlaucoma was induced in both eyes of each animal under sterile condition.\nInducing glaucoma in both eyes while treating only one eye makes the fellow eye’s status critical for inference, because it is the primary comparator for treatment effects. When both eyes share systemic circulation, anesthesia, stress, and other animal-level influences, the fellow eye is not an independent unit and can be influenced by treatment applied to the other eye. This strengthens the need to rule out contralateral pharmacologic effects and to analyze the data with paired-eye considerations. Without such controls, the within-animal comparison may conflate local drug delivery effects with systemic or cross-eye effects. In addition, bilateral disease induction can amplify shared inflammatory or physiologic changes that affect both eyes’ outcomes. Thus, this design choice increases sensitivity to contralateral confounding rather than eliminating it.\nGlaucoma therapeutic eye drop (0.5% Timoptic, Bausch Lomb) into the right eye and saline instilled into the left eye were performed twice a day.\nThis sentence confirms that the contralateral-eye control is not merely a one-time comparison but is repeatedly used during a treatment regimen. Repeated dosing increases the opportunity for systemic absorption and sustained contralateral effects, making confounding more likely if not explicitly tested. It also shows the control eye is exposed to an “active” experimental context (handling, instillation, potential systemic exposure) rather than being a naive baseline. If systemic timolol lowers IOP in the left eye, then the paper could underestimate differences between treated and “control” eyes or misattribute bilateral changes to disease progression rather than pharmacology. This weakens the interpretation of both IOP outcomes and histologic/biomarker endpoints that depend on IOP control. A standard mitigation would be to include an independent untreated-animal control group for therapeutic comparisons or to quantify contralateral IOP effects explicitly.\nThese findings suggest the contralateral reduction in intraocular pressure from timolol is caused by systemic absorption. ([1](#ref1))\nThis literature statement directly supports the concern that timolol delivered to one eye can lower IOP in the fellow eye, violating the paper’s assumption that the contralateral eye is an untreated control. The cited work is specifically about contralateral IOP reduction after unilateral timolol administration, making it highly relevant to the paper’s experimental design. Because the paper’s therapeutic conclusions rely on comparisons between treated right eyes and contralateral control left eyes, systemic absorption creates a plausible, evidence-based alternative explanation for observed effects. This does not prove the paper’s results are wrong, but it shows the study design is vulnerable to a well-documented pharmacologic confound. In high-stakes translational claims (theranostic glaucoma control), such confounding must be ruled out with dedicated controls or measurements. Without that, the therapeutic-efficacy conclusion is less reliable.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|GPT|2", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "This paper’s in vivo therapeutic-efficacy and biosafety conclusions are drawn from very small group sizes and an insufficiently specified statistical approach that does not clearly define the experimental unit (animal vs eye vs repeated measures), making the reported significance claims and inferred robustness of treatment effects unreliable.\n\nThe glaucoma induced rabbits and normal rabbits were divided into 3 groups to assess the therapeutic effects of smart contact lens and eye drop: Glaucoma induced by MC or α-chymotrypsin with eye drop (n = 3, group 1), glaucoma induced by MC or α-chymotrypsin with smart contact lens (n = 3, group 2), and the normal rabbits as a control (n = 3, group 3).\nThis sentence shows the core therapeutic comparisons are based on n=3 rabbits per group, which is a very small sample for drawing robust conclusions about disease modification and biomarker changes. With such small n, estimates of variability are unstable and p-values can be highly sensitive to outliers or non-normality, especially in biological endpoints like histology and immunohistochemistry. The paper makes strong claims (e.g., prohibiting progression of glaucoma) that imply reliability across individuals, but n=3 provides limited evidence for generalizability. Small-n designs can be appropriate for feasibility demonstrations, but then the conclusions should be correspondingly circumscribed and uncertainty should be emphasized with effect sizes and confidence intervals. Here, the paper presents the group sizes but does not, in the quoted sentence, justify them or connect them to a primary endpoint. This gap undermines confidence in the statistical robustness of the therapeutic claims.\nAfter 7 days of glaucoma induction, the treatments were performed on right eyes of rabbits and non-treatments were performed on left eyes of rabbits.\nThis sentence indicates a paired-eye within-animal design, where each rabbit contributes both a treated and a “non-treated” eye. In such designs, the experimental unit is often the animal (or paired eyes), and analyses need to account for within-animal correlation rather than treating eyes or measurements as independent. If the paper’s statistical testing instead pools eyes or repeated measurements without hierarchical or paired modeling, significance can be inflated due to violated independence assumptions. The description does not specify whether outcomes are analyzed per animal, per eye, or per measurement timepoint, making it difficult to assess correctness. Because therapeutic conclusions hinge on these comparisons, unclear handling of pairing is a substantive threat to validity rather than a cosmetic reporting issue. Standard practice is to predefine the experimental unit and use paired tests or mixed-effects models when appropriate.\nWe performed one-sided statistical analyses using one-way analysis of variance (ANOVA). For all experiments, *P < 0.05, **P < 0.01 and ***P < 0.001 were considered statistically significant.\nThis statistical description is too coarse to evaluate whether the reported p-values are appropriate for the study design and data structure. One-way ANOVA assumes independent observations and (typically) homoscedastic residuals; neither assumption is addressed here, despite paired-eye designs and repeated IOP measurements described elsewhere. The paper also does not specify the post-hoc procedure, multiple-comparison corrections, or which outcomes were tested with which model, which is essential when many endpoints (IOP trajectories, histology, multiple biomarkers) are assessed. The phrase “one-sided statistical analyses” is also unusual in this context and heightens the need for explicit justification and preregistration of directional hypotheses, particularly with small n. Without a clearer mapping from endpoints to models and assumptions, the claimed statistical significance cannot be independently verified. This directly weakens the reliability of the paper’s therapeutic and biosafety conclusions.\nSample size | 2 | a. Specify the exact number of experimental units allocated to each group, and the total number in each experiment. Also indicate the total number of animals used.  b. Explain how the sample size was decided. Provide details of any a priori sample size calculation, if done. ([2](#ref2))\nThis guideline statement clarifies that good animal-study reporting requires both exact group sizes and an explanation of how sample size was determined, ideally via an a priori calculation for hypothesis-testing work. While the paper reports n=3 per group, it does not provide (in the quoted methods/statistics text) an explanation of how that n supports the key therapeutic endpoints. The guideline also frames sample size in terms of “experimental units,” which is critical in paired-eye and repeated-measures settings where the animal is often the unit. In the paper, the experimental unit is not clearly stated, and the statistical method description does not address the dependence structure. This mismatch between recommended reporting and what is provided reduces confidence that the analysis supports the strength of the conclusions. Given the translational framing (“theranostic… platform”), these reporting and design gaps are substantial.\nTreating multiple cells from a single animal as independent for statistical analysis is pseudoreplication and can result in bogus estimates of significance. ([3](#ref3))\nAlthough this quote discusses multiple cells, the same statistical principle applies to any clustered measurements within an animal, including multiple eyes and repeated measurements over time. The paper’s design includes within-animal clustering (e.g., right vs left eye) and repeated IOP readings, which can lead to inflated type I error if analyzed as independent samples. The paper’s statistical description does not indicate use of hierarchical/nested approaches or paired analyses that respect clustering. With n=3 animals per group, the temptation to increase apparent sample size by using many measurements is particularly strong, and the risk of pseudoreplication becomes more consequential. This literature reinforces that independence is not a technical detail but a core validity requirement for inferential statistics. Therefore, without explicit clarification of the experimental unit and clustering-aware analysis, the reported significance claims are not dependable.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|GPT|3", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "This paper’s central methodological claim—quantitative IOP monitoring in mmHg by a smart contact lens—relies on per-rabbit calibration curves using tonometer readings, which limits interpretability as a direct measurement and undermines the paper’s implicit generalizability of mmHg readouts across subjects and time.\n\nThe output codes were collected for 30 min at the interval of 5 min. After 30 min, the smart contact lens was removed from the rabbit’s eye and the IOP was measured with a tonometer again. The output codes were converted into IOP (mmHg) based on our calibration standard curve for each rabbit.\nThis description makes clear that the contact lens does not directly output IOP in mmHg; instead, it outputs “codes” that must be converted using an individualized calibration curve. As a result, the claimed mmHg values are a derived quantity anchored to tonometer readings, not a standalone sensor measurement. This matters because a clinically useful mmHg readout would ideally be robust across subjects and not require extensive per-patient calibration against conventional tonometry. The sentence also implies the lens is removed and tonometry is used again, reinforcing that conventional measurement remains integral to generating and validating the mmHg numbers. Without evidence that the calibration remains stable across days, repositioning, or physiological changes, the mmHg conversion may be fragile. Therefore, the quantitative conclusion (“IOP… monitored”) depends materially on calibration procedures rather than intrinsic sensor accuracy.\nThe recorded output code was 0 mmHg before wearing smart contact lens and the output code was measured at more than two different IOP levels after wearing smart contact lens.\nThis sentence indicates that “0 mmHg” is used as a pre-wear baseline code, which is not a physiologically meaningful IOP value, and underscores that the system’s mapping to mmHg is constructed rather than directly sensed. Establishing a baseline “without wearing” also introduces a procedural dependency: the mmHg output depends on how baseline and tension-free conditions are defined and reproduced. The need for “more than two different IOP levels” suggests multi-point calibration, but the paper does not, in this result section, describe how those IOP levels are produced or controlled in vivo in a way that could be replicated across labs. Because calibration is per rabbit and apparently depends on eye size and fit, the resulting mmHg readouts may not generalize even within the same species, let alone to humans. This weakens the strength of the paper’s conclusion that the device provides quantitative IOP monitoring comparable to clinical tonometry. A more convincing demonstration would include stability/transferability of calibration and error analysis across sessions and subjects.\nTo obtain the standard graph of each rabbit to convert code change to IOP level, the base codes of smart contact lens were measured before wearing smart contact lens without any tension (0 mmHg, \\( C_0 \\)). The IOP level of each rabbit was measured by tonometer (\\( \\chi \\) mmHg). Right after that, the code outputs were measured by wearing smart contact lens (\\( \\chi \\) mmHg, C). The code changes obtained by equation (1) were matched with IOP changes with more than 2 points. The slope of standard graph of each rabbit was used to convert code changes (%) to IOP changes (mmHg) for each rabbit using equation (2).\nThese supplementary-method sentences provide the mathematical mechanism by which “IOP (mmHg)” is produced: an individualized slope S is estimated per rabbit from paired tonometer-and-lens measurements. This confirms the device’s mmHg output is contingent on a calibration step that itself uses conventional tonometry and depends on the specific rabbit. The need to estimate S per rabbit aligns with known concerns that contact-lens strain signals can reflect a composite of IOP-related deformation and biomechanical factors, which vary across eyes. The calibration procedure also creates additional sources of uncertainty (e.g., tonometer error, fit variability, and limited calibration points) that should be propagated into error bars or confidence intervals for the lens-derived mmHg readouts, but such uncertainty reporting is not explicit in the main claims. Because the paper’s headline conclusion emphasizes monitoring and control of IOP, the dependence on individualized calibration is not a minor implementation detail—it is central to whether the numbers are interpretable as true IOP. This limits the strength and generality of the quantitative monitoring claim.\nOne major limitation of the CLS is that its output cannot be converted to millimeter mercury (mmHg) to allow for direct clinical interpretation. ([4](#ref4))\nThis literature statement highlights a widely recognized limitation in contact-lens-based IOP sensing: outputs often cannot be straightforwardly converted to mmHg because they do not measure IOP directly. The paper under review addresses this by performing per-rabbit calibration, but that solution shifts the burden to individualized calibration procedures rather than demonstrating a generalizable mmHg sensor. Given that prior work frames mmHg conversion as a major limitation, a strong paper claiming quantitative mmHg monitoring should thoroughly validate calibration stability, cross-subject transfer, and clinically meaningful accuracy bounds. The reviewed paper’s main narrative emphasizes successful monitoring and control, but the reliance on per-rabbit slopes indicates the device is closer to an IOP-related pattern sensor plus calibration pipeline. This is not necessarily invalid, but it materially changes what can be concluded about the device’s standalone quantitative capability. Therefore, the paper’s conclusions about mmHg monitoring require more careful qualification and validation than currently supported.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|GPT|4", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "The paper claims continuous, real-time monitoring and IOP-responsive drug delivery via a feedback system, but the in vivo demonstrations measure IOP over short intervals and implement drug release on a coarse, scheduled timescale; this weakens the conclusion that the system provides clinically relevant continuous closed-loop IOP management.\n\nAccordingly, it is important to monitor continuous IOP changes in real time and deliver drugs in response to the IOP profiles.\nThis sentence sets a high bar for the clinical and technical goal: continuous, real-time monitoring coupled to responsive therapy based on the IOP profile. In glaucoma, the motivation for such systems is precisely that IOP varies dynamically and peaks may be missed by sporadic clinic measurements. Therefore, an adequate validation would typically demonstrate monitoring over extended diurnal/nocturnal periods and therapy decisions triggered in real time by measured IOP changes. The paper’s later in vivo protocol, however, involves short monitoring windows and device removal, which does not match the “continuous… in real time” aspiration. This mismatch matters because the key claimed advantage over standard care hinges on capturing dynamics outside conventional measurement times. Without extended continuous validation, the conclusion about profile-responsive control is less robust.\nThe output codes were collected for 30 min at the interval of 5 min. After 30 min, the smart contact lens was removed from the rabbit’s eye and the IOP was measured with a tonometer again.\nThis methods description indicates that the device’s in vivo monitoring is performed for a 30-minute window with 5-minute sampling, followed by removal and confirmatory tonometry. Such a protocol demonstrates feasibility of short-term sensing but does not establish the ability to continuously monitor IOP over hours to days, including undisturbed sleep or typical daily activity. Because the paper’s framing emphasizes continuous monitoring and a feedback system, the temporal scope of validation is a core methodological limitation. Removing the lens also introduces discontinuities and may prevent evaluating longer-term drift, fit changes, or sensor stability—issues that are central to continuous-wear devices. Furthermore, short-window monitoring makes it harder to show the system can detect and respond to spontaneous IOP peaks that occur outside brief test sessions. Thus, the evidence provided supports short-term proof-of-concept rather than clinically relevant continuous monitoring.\nFinally, the IOP level was controlled with the theranostic smart contact lens by monitoring IOP and releasing timolol every other day for 5 days (Fig. 6e).\nThis sentence describes the therapeutic “control” protocol as releasing timolol every other day across five days, which is a coarse schedule rather than a continuously adaptive closed-loop controller. While the authors narrate decisions like “timolol was not released” when IOP was normal, the control cadence (days) is far slower than the intra-day fluctuations that motivate continuous IOP monitoring. In closed-loop systems, a key methodological expectation is that actuation is triggered by sensor readings in a timely manner with a defined control policy; here, the protocol resembles intermittent dosing with monitoring rather than continuous feedback control. This matters for conclusions because a system that only adjusts therapy every other day may not prevent short-lived peaks or nocturnal elevations. Therefore, the evidence does not fully justify the strong claim of continuous IOP-responsive control.\nIn the present study, we noted that two-thirds of the glaucoma patients had their IOP peak outside office hours. ([5](#ref5))\nThis clinical observation from the literature underscores why continuous or diurnal-scale monitoring is valuable: many clinically relevant IOP peaks occur outside standard measurement windows. The reviewed paper’s in vivo monitoring windows (tens of minutes) are analogous to “office-hour snapshots” rather than a diurnal profile, so they are unlikely to capture peak timing reliably. The literature therefore provides a concrete benchmark for what “continuous” monitoring must address—capturing peaks that occur at unpredictable times. When a paper claims continuous real-time monitoring and feedback control, demonstrating performance across such peak periods is central to validating the clinical premise. Without such validation, the manuscript’s conclusions about clinical relevance and the significance of the feedback system are weakened. The cited literature does not contradict feasibility claims but shows that the demonstrated protocol is not aligned with the problem definition.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|GPT|5", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "The paper presents a highly integrated wireless/ASIC-enabled theranostic platform, but the provided code is not sufficient to reproduce the reported telemetry, decoding, and control workflow because it is incomplete and tied to specific lab hardware/software assumptions.\n\nHere, we report a precisely integrated theranostic smart contact lens with a sensitive gold hollow nanowire (AuHNW) based IOP sensor, a flexible drug delivery system (DDS), wireless power and communication systems and an application specific integrated circuit (ASIC) chip for both monitoring and control of IOP in glaucoma.\nThis abstract claim emphasizes an end-to-end integrated system (sensor + DDS + wireless power/communication + ASIC) and implies that the telemetry/control stack is a central contribution. For such a system, reproducibility depends not only on materials fabrication but also on the digital communication, decoding, and control logic that turns raw signals into actionable measurements and actuation triggers. The manuscript describes “output codes” and calibration-driven conversion to mmHg, but without runnable code and clear interfaces, independent verification of the telemetry and decoding pipeline is difficult. Because the system’s performance claims depend on correct code-to-IOP decoding and correct triggering of drug release, incomplete code undermines methodological transparency. This is especially important when “feedback system” and wireless operation are key claims. Therefore, code completeness is directly tied to reproducibility of the core system claims.\n```verilog\n//////////////////////////////////////////////////////////////////////////////////\n// PWM transmitter + LSK demodulator code. (RS232 serial communication with PC)\n// Created by JCH\n//\tPin assignment for DSP-PLUS II board (company : Libertron)\n//  <Port name>\t\t<FPGA Board name>\n//\t\ti_Clock\t\t\t(internal clock)\t\t\t\n//\t\tPWM_OUT\t\t\t\t\n//\t\tPWM_ENABLE\t\t\t\n//\t\tLSK_IN\t\t\t\t\n//\t\to_Tx_Serial\t\t\t\n//\t\to_Tx_Serial_Test\n//\t\n//////////////////////////////////////////////////////////////////////////////////\nmodule LSK_v1(i_Clock,DIP_SW,LED_OUT,PWM_OUT, PWM_ENABLE, LSK_IN, o_Tx_Serial, o_Tx_Serial_Test\n     //,data_tx\n\t );\n```\nThis code header shows the shared Verilog targets a specific FPGA development board (“DSP-PLUS II board”) and an RS232 PC link, which is not the same as sharing the ASIC design described in the paper. The module interface includes DIP switches and LED outputs, consistent with a lab evaluation setup rather than an integrated wearable system artifact that others can fabricate or simulate to match the paper’s in vivo platform. The paper’s claims center on an “ultra-low power” ASIC and integrated wireless telemetry, but the repository does not include the ASIC RTL, verification environment, or documentation linking this FPGA code to the reported animal experiments. Without testbenches, protocol specifications, and parameterization matching the manuscript’s reported sampling and “output codes,” the code cannot be used to reproduce the decoding/measurement pipeline. In reproducibility terms, hardware-specific scaffolding without the full integrated stack is insufficient for independent replication. This gap limits the transparency of the wireless communication and control components central to the paper’s contribution.\n```java\npublic String Filepath=\"D:\\\\Dropbox\\\\0_JAVA\\\\txt_file\";\npublic File file = new File(\"D:\\\\Dropbox\\\\0_JAVA\\\\txt_file\");\n...\n//private data data= new data();\nprivate datam datam= new datam();\n```\nThis Java code snippet demonstrates that the provided desktop-side tooling is not self-contained: it hard-codes a local Windows path and instantiates a `datam` class that is not included in the shared code. It also depends on external libraries (e.g., `gnu.io.*` for serial communication and JFreeChart) that are not packaged with the repository, making compilation and execution non-trivial without additional context. Because the manuscript relies on “output codes” collected during in vivo tests and then converted into IOP via calibration, the absence of complete decoding/processing code prevents others from reproducing the exact data-processing steps. In systems papers, the ability to reconstruct the signal-processing pipeline is essential to validate claims such as sampling interval, filtering, outlier handling, and code-change computation. The incompleteness therefore impacts reproducibility of the measurement and control workflow rather than being a minor software engineering issue. Consequently, the paper’s methods are not sufficiently transparent to enable independent reproduction of the full system behavior.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "The paper proposes a drug delivery mechanism based on the electrochemical dissolution of gold, which releases gold ions into the eye. This poses a significant safety risk as gold ions can be toxic to ocular tissues, yet the paper fails to adequately address or evaluate this toxicity.\n\n\"The flexible DDS could release timolol on-demand by the electrochemical dissolution of gold channels.\"\nThis statement describes the core mechanism of the drug delivery system. The \"dissolution\" implies that the gold material is oxidized and released into the surrounding environment (the tear film and ocular surface) as ions.\n\"During molding process, the gold channel and the cathode were open to allow gold dissolution by the electrochemical reaction of gold in the tear.\"\nThis confirms that the dissolution occurs directly in the tear fluid, meaning dissolved gold species will come into direct contact with the cornea and other ocular tissues.\n\"Gold compounds can produce 2 types of ocular lesions—chrysiasis and inflammation or ulceration of the cornea.\" [1]\nThis literature establishes that gold compounds and particulate gold can be toxic to the eye, causing specific lesions. The release of gold ions via electrochemical dissolution creates a risk of such toxicity, which the authors do not evaluate.\n\"Gold ions are toxic for almost all organisms, due to its high oxidizability.\" [2]\nThis general toxicological principle highlights the danger of releasing gold ions. Unlike stable gold nanoparticles, gold ions are highly reactive and can cause cellular damage. The paper's failure to assess the concentration and toxicity of the released gold ions renders the safety claims unsupported.\n\nReferences:\n[1] Grant, W. M., & Kern, H. L. (1956). Action of gold on the cornea. *Investigative Ophthalmology & Visual Science*. (Note: The specific quote about \"2 types of ocular lesions\" is referenced in *Ulcerative Keratitis Following Particulate Elemental Gold Deposition*, Cornea, 2011. https://pubmed.ncbi.nlm.nih.gov/21993463/)\n[2] Comparison of gold ion and nanoparticle toxicity. *ScienceDirect Topics*. https://www.sciencedirect.com/topics/materials-science/gold-ion", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "The proposed IOP sensor relies on an individual calibration method that requires establishing a specific standard graph for each subject. This approach is impractical for clinical use, as it would likely require invasive procedures to manipulate IOP in patients to generate the calibration curve.\n\n\"The slope of standard graph of each rabbit was used to convert code changes (%) to IOP changes (mmHg) for each rabbit using equation (2).\"\nThis quote from the supplementary materials reveals that the sensor's output was converted to IOP using a subject-specific slope. This implies that the sensor's response is not universal and varies between individuals.\n\"To obtain the standard graph of each rabbit to convert code change to IOP level, the base codes of smart contact lens were measured before wearing smart contact lens without any tension... The IOP level of each rabbit was measured by tonometer... The code changes obtained by equation (1) were matched with IOP changes with more than 2 points.\"\nThe calibration process described involves measuring multiple points to establish a slope for each rabbit. In a clinical setting, it is not feasible to artificially induce significant IOP changes in a patient to calibrate the lens. This limitation severely restricts the practical applicability of the device.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "The device generates excessive heat, reaching temperatures significantly higher than the normal ocular surface temperature. This poses a risk of thermal injury or discomfort to the user, which is not adequately addressed by the authors' claim of \"no critical thermal damages.\"\n\n\"Although the temperature of chip increased up to 39.3 °C, there were not any critical thermal damages on the cornea after finishing all in vivo tests.\"\nThe authors admit that the chip temperature reached 39.3 °C. While they claim no damage was observed, this temperature is well above the normal ocular surface temperature.\n\"The ocular surface temperature of the central cornea is normally around 35°C...\" [3]\nThis literature value (~35°C) serves as a baseline. A temperature of 39.3°C represents an elevation of over 4°C. Prolonged exposure to such temperatures could lead to discomfort, inflammation, or subtle thermal damage that might not be immediately visible but could be harmful over time.\n\"Thresholds for thermal damage to cornea tissue... is related to a temperature rise of about 35°C above the normal corneal temperature...\" [4]\nWhile the immediate damage threshold might be higher, medical device standards (e.g., IEC 60601-1) often set lower limits for parts in continuous contact with sensitive tissues to prevent long-term injury or discomfort. The paper lacks a thorough investigation into the long-term thermal safety of the device.\n\nReferences:\n[3] Purslow, C., & Wolffsohn, J. S. (2005). Ocular surface temperature: a review. *Eye & Contact Lens*, 31(3), 117-123. https://pubmed.ncbi.nlm.nih.gov/15894878/\n[4] Peppers, N. A., et al. (1969). Corneal damage thresholds for CO2 laser radiation. *Applied Optics*, 8(2), 377-381. https://opg.optica.org/ao/abstract.cfm?uri=ao-8-2-377", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "The paper evaluates the performance of the AuHNW sensor primarily by comparing it to its precursor (Ag@AuNW), ignoring other state-of-the-art IOP sensors such as those based on graphene or other advanced nanomaterials. This limited comparison fails to demonstrate the true superiority or significance of the proposed material.\n\n\"AuHNW showed higher sensitivity than Ag@AuNW with a reasonable stretchability of 30% (Fig. 2g).\"\nThe authors highlight the improvement over Ag@AuNW, which is an internal baseline. However, they do not compare the sensitivity, drift, or hysteresis of their sensor with other leading technologies mentioned in their own introduction.\n\"Highly Transparent and Sensitive Graphene Sensors for Continuous and Non-invasive Intraocular Pressure Monitoring.\" [5]\nThis cited paper (Ref 13 in the manuscript) presents a graphene-based sensor. The authors should have compared their AuHNW sensor's performance metrics (e.g., gauge factor, detection limit) with such state-of-the-art alternatives to justify the novelty and advantage of their approach.\n\"A soft and transparent contact lens for the wireless quantitative monitoring of intraocular pressure\" [6]\nThis is another relevant high-impact study (Ref 12 in the manuscript). A direct comparison with the performance of the sensor in this study would have provided a more objective assessment of the AuHNW sensor's standing in the field.\n\nReferences:\n[5] Xu, J., et al. (2020). Highly Transparent and Sensitive Graphene Sensors for Continuous and Non-invasive Intraocular Pressure Monitoring. *ACS Applied Materials & Interfaces*, 12(16), 18375-18384. https://pubs.acs.org/doi/10.1021/acsami.0c00324\n[6] Kim, J., et al. (2021). A soft and transparent contact lens for the wireless quantitative monitoring of intraocular pressure. *Nature Biomedical Engineering*, 5, 772-782. https://www.nature.com/articles/s41551-021-00719-w", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Gemini|5", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "The in vivo experiments were conducted with a very small sample size (n=3 per group), which is insufficient to draw statistically robust conclusions regarding the efficacy and safety of the device.\n\n\"The glaucoma induced rabbits and normal rabbits were divided into 3 groups... (n = 3, group 1), glaucoma induced by MC or α-chymotrypsin with smart contact lens (n = 3, group 2), and the normal rabbits as a control (n = 3, group 3).\"\nUsing only 3 animals per group is statistically weak and prone to Type I or Type II errors. Biological variability is high, and such a small sample size cannot reliably demonstrate the therapeutic effect or safety profile of the device.\n\"We performed one-sided statistical analyses using one-way analysis of variance (ANOVA). For all experiments, *P < 0.05... were considered statistically significant.\"\nWhile statistical tests were performed, the validity of ANOVA on such a small sample size is questionable. A larger sample size is standard practice in preclinical studies to ensure reproducibility and reliability of the results.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "Why was a Ag@AuNW chosen as a control and not simply AuNW?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "What is the thickness of the films for characterization in Figure 2? Especially we note that the authors compared its relative resistance change with a 100 nm Au film. It would be good if the authors can also specify the thickness of the AuHNW film.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "It is important to characterize the chemical stability of the materials. Is there any reason for choosing H2O2 for the testing?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "Although the AuHWN is quite transparent and shows a good transmittance (Figure 2e,f), the DDS device with the ASIC chip is completely opaque. It would be good if the author can also consider the transmittance of the whole device as a benchmark.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "Figure 2g shows a very large change in resistance of over 10,000% at 30% strains. It is unclear how the devices were contacted. Also, what was the initial resistance of the film? The authors did not state whether it was a two-point or four-point probe measurement that eliminates the contact resistance effect. More details should be provided on the electromechanical characterizations.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "As a proper control, a contact lens device made using Ag@AuNW should be made and IOP relationship determined.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "There was a lack of details on the ASIC chip. While I understand the major point of this paper is the use of hollow AuNWs, more information on the ASIC should be provided, e.g., power consumption, circuit blocks, etc.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "What is the effect on the IOP for different human behaviours, for example eye blinking, closed eye, lying down etc? If they cause IOP fluctuation, is the device able to cater to different conditions?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Human_1|9", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "Figure 6b shows a relatively large spread in the values between what was measured in the contact lens vs. tonometer. Can the authors explain why? There was also less data collected at higher IOPs.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Human_1|10", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "Supp Fig 9 shows a side profile of the lens fitting. Can the authors provide top view as well? How is the perfect fitting determined?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Human_1|11", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "Supplementary Figure. 3b is missing the scale bar?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "There should be a discussion about diurnal-nocturnal IOP fluctuation. How does the proposed system determine changes and release the drug beyond the IOP fluctuation?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "A discussion on how the patient will use the proposed smart contact lens is needed. Will this be worn daily? Weekly wear? (clearly define their short-term vs. long-term monitoring in terms of hours, days, weeks, months)", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "A discussion of why hallow nanomaterial is better (advantage) than bulk is needed.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "The authors stated that 30% stretchability is reasonable. How was this determined? What would be the optimal stretchability? (similar to the current contacts lens?)", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "How does the device perform at a higher IOP (above 35 mm Hg)? How often would the drug release be triggered if the IOP does not respond to the treatment?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "The amount of drug loaded was based on one drop of commercial eye drop. Much of the drug is lost with the eye drop before penetration into the eye. Does the contact lens provide better drug availability and facilitate diffusion into the eye? Should a lower amount be used?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "Consider including the drug release complete profile with one reservoir within the main manuscript.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "It is not clear what Figure 4G demonstrates. Is this a cumulative amount of drug release?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "Clearly state how long the animals had contact lenses on for the biosafety study.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Human_2|10", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "Figure 6 should show the IOP readings on Day 2 and Day 4. Does the treatment provide a relatively sustained decrease in IOP these days? How fast does IOP increase as the drug therapeutic is decreasing? What was the rationale for treating every other day with the device?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "With only a few reservoirs, the lens would need to be replaced regularly. For a once daily drug, this might happen at just a few day intervals. For a twice daily drug, it might be every 2 days. For a drug administered more frequently, it might be daily. This could be a major impediment to its use. Would such an approach with this lens be safe? (eg risk to corneal epithelium and keratitis, ulcer, etc) How can this be addressed?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "The drug is released over ~30 min. How does this influence efficacy and safety compared to an eye drop that is released as a bolus? Bathing tissue with a drug is very different from brief exposure. The efficacy studies are performed with two poorly reproducible models (alpha-chymo and methycellulose). It is unclear why you employed these models and evaluated so few rabbits?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "L30 IOP does not indicate glaucoma condition as majority of individuals with high iOP do not have glaucoma and as many as one half of patients with glaucoma do not have high IOP.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "L34 Tonometry is typically not uncomfortable. Tonometers are not typically thought to be expensive. With current instruments, clinical training needed is minimal and the measurements are easy to perform with just a few minutes of training.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "L36 Unclear what is meant by “critical mismatch” –IOP varies throughout the day and also day to day.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|52|Human_3|7", "source": "prb", "split": "test", "paper_id": "prb52", "comment": "L38 Adherence is a problem with eye drop treatment, however the text is inaccurate.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|53|Claude|1", "source": "prb", "split": "test", "paper_id": "prb53", "comment": "The paper does not provide any statistical validation or false discovery rate (FDR) estimation for the spectral matches between experimental spectra and the microbeMASST reference database. The default search parameters (cosine ≥ 0.7, minimum 3 matching peaks) are heuristics that have been shown to require adjustment for different datasets and do not provide statistical confidence estimates.\n\n\"Searches are customizable and default settings are the following: precursor and fragment ion mass tolerances = 0.05, minimum cosine score threshold = 0.7, minimum number of matching fragment ions = 3, and analog search = False.\"\nThe paper uses fixed heuristic thresholds for spectral matching without providing any validation of the false positive rate at these thresholds. While these parameters are commonly used in the field, their appropriateness varies significantly by dataset. The minimum matched peaks threshold of 3 is notably lower than the community standard of 6, which could substantially increase false positive matches. The paper does not justify this parameter choice or assess its impact on match reliability.\n\"such heuristics do not provide a statistical confidence estimate of the spectrum annotations, and as such, the number of false positives (i.e. incorrectly accepted high-scoring annotations) and false negatives (i.e. missed low-scoring annotations) are unknown... Although not widely used yet at this time, there are emerging strategies for estimating the false discovery rate of MS/MS spectrum annotations.\" [[1]](#citation-1)\nThe metabolomics community has recognized that fixed cosine thresholds do not provide statistical confidence in spectral annotations. This published review from PMC explicitly notes that using cosine thresholds like 0.7 without FDR estimation leaves the number of false positives unknown. The microbeMASST paper's claim of identifying 512 \"putative microbial metabolites\" cannot be evaluated without knowing how many of these matches might be false positives.\n\"Passatutto produced decoy spectra for GNPS's spectral library search workflows... By adjusting the scoring parameters and thresholds, the number of annotations rose, on average, by +139% (ranging from −92 up to +5705%) when compared with a default parameter set available at GNPS.\" [[2]](#citation-2)\nThis Nature Communications study demonstrates that optimal spectral matching parameters vary dramatically between datasets. Using default GNPS parameters led to annotation rates that varied from 92% underestimation to 5705% overestimation compared to FDR-controlled parameters. The microbeMASST paper's use of fixed default parameters without dataset-specific validation means the actual false discovery rate of their 512 putative microbial metabolites is unknown and could be substantially higher than assumed.\n\nReferences:\n[1] [Spectral Libraries - Metabolomics Community Knowledge, PMC10284100](https://pmc.ncbi.nlm.nih.gov/articles/PMC10284100/)\n[2] [Significance estimation for large scale metabolomics annotations by spectral matching, Nature Communications 2017](https://pmc.ncbi.nlm.nih.gov/articles/PMC5684233/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|53|Claude|2", "source": "prb", "split": "test", "paper_id": "prb53", "comment": "The paper's core experimental workflow assumes that MS/MS spectra present exclusively in colonized (SPF) mice and absent in germ-free (GF) mice must be microbial in origin. However, this inference is flawed because host metabolism is substantially altered by microbial colonization, meaning many of these metabolites could be host-derived but microbiota-induced rather than directly synthesized by microbes.\n\n\"We extracted 10,047 consensus MS/MS spectra uniquely present in SPF mice and queried them with microbeMASST. A total of 3,262 MS/MS spectra were found to have a microbial match... these 512 were only present in animals not treated with antibiotics.\"\nThe experimental design selects for metabolites present in colonized animals but absent in germ-free animals, then further filters by absence in antibiotic-treated animals. However, this approach cannot distinguish between metabolites directly synthesized by microbes versus metabolites synthesized by the host in response to microbial colonization. The germ-free mouse model causes profound changes in host physiology, including altered immune function, intestinal morphology, and host metabolic pathways. Many metabolites that appear only in colonized animals are synthesized by host tissues that are developmentally or functionally dependent on the microbiome, not by the microbes themselves.\n\"One interpretation of this finding is that microorganisms are capable of producing metabolites previously described to only be made by mammalian hosts. Notable examples include serotonin, γ-aminobutyric acid (GABA), and the glycocholic acid, with microorganisms often being the primary producers of these metabolites in the gut. Additionally, an alternative hypothesis is that microorganisms can also selectively stimulate the production of host metabolites.\"\nThe authors acknowledge this limitation at the end of the Results section but do not adequately account for it in their workflow or conclusions. The presence of serotonin and GABA—well-known host neurotransmitters—in their \"microbial metabolite\" list suggests significant contamination of their putative microbial metabolite set with host-derived molecules. While microbes can produce these molecules, the majority of intestinal serotonin is produced by host enterochromaffin cells that are stimulated by microbial signals. The authors' alternative hypothesis (microbes stimulating host production) directly contradicts their claim that these are \"microbial-derived\" metabolites.\n\"The authors continued their investigation of time-of-day differences in host metabolism by performing metabolomics of the liver and blood... They found that both during the light and dark phases, the metabolomes of OligoMM12 mice were consistently more similar to those of GF mice than SPF mice. This finding suggests that this minimal microbiome is unable to fully reproduce the effects of a conventional microbiome on the host metabolome.\" [[3]](#citation-3)\nThis published study demonstrates that microbial colonization has profound effects on the host metabolome that extend far beyond direct microbial metabolite production. The finding that host tissue metabolomes (liver and blood) differ substantially between GF and SPF mice indicates that many metabolites detected only in colonized animals result from altered host metabolism rather than direct microbial synthesis. The microbeMASST workflow does not account for this biological complexity.\n\nReferences:\n[3] [Microbiome complexity shapes metabolism, PLOS Biology](https://journals.plos.org/plosbiology/article?id=10.1371/journal.pbio.3001793)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|53|Claude|3", "source": "prb", "split": "test", "paper_id": "prb53", "comment": "The workflow removes 837 MS/MS spectra from consideration because they also matched human cell lines. However, many metabolites are produced by both microbial and mammalian metabolic pathways, so this filtering step may inappropriately exclude genuine microbial metabolites that happen to also be present in human cells.\n\n\"A total of 3,262 MS/MS spectra were found to have a microbial match. Of these, 837 were also found in human cell lines and for this reason were removed from further analysis.\"\nThis filtering removes 25.7% (837/3,262) of spectra with microbial matches. The logic assumes that if a metabolite is found in both microbial monocultures and human cell lines, it cannot be attributed to microbes. However, this overlooks the extensive overlap in primary metabolism between microbes and mammals. Metabolites like amino acids, nucleotides, and many lipids are synthesized by both domains of life. Excluding these removes information about bona fide microbial metabolic activity in the gut.\n\"Primary bile acids, including cholate (CA) and chenodeoxycholate (CDCA), are synthesized by hepatocytes... Approximately 5% of bile acids are converted into secondary bile acids by a limited number of microbiota species... in the cecum and colon.\" [[4]](#citation-4)\nBile acid metabolism exemplifies metabolites with both host and microbial origins. Primary bile acids are synthesized by the liver (and would be present in human cell lines), but microbial modification produces secondary bile acids. The authors highlight bile acid conjugates as key findings, yet their filtering approach based on human cell line presence could inappropriately exclude metabolites where both host and microbial contributions exist. The binary classification (microbial OR human) does not capture the biological reality of shared metabolic pathways.\n\nReferences:\n[4] [Bile acids as modulators of gut microbiota composition and function, PMC9904317](https://pmc.ncbi.nlm.nih.gov/articles/PMC9904317/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|53|Claude|4", "source": "prb", "split": "test", "paper_id": "prb53", "comment": "The microbeMASST reference database derives taxonomic assignments from user-submitted metadata without genetic verification, which the authors acknowledge in limitations. Published studies estimate that 3.6% of prokaryotic genome taxonomic annotations in GenBank are incorrect. This error rate would propagate incorrect microbial producer attributions throughout the tool's results, which is significant given that linking metabolites to producers is the tool's core function.\n\n\"Taxonomic tree was generated using associated NCBI IDs provided by the community. Specimen assignment prior to metabolomic analysis can not be checked by microbeMASST. The majority of the deposited data do not have associated genetic information and even if available, it was not used to build taxonomic tree. Thus, specimen mis-identification is possible.\"\nThe authors acknowledge this limitation in the Technical Limitations section. However, given that the core value proposition of microbeMASST is linking metabolites to specific microbial producers via the taxonomic tree, specimen misidentification directly undermines the tool's primary function. A user searching for the microbial origin of a compound would receive incorrect producer information in a significant fraction of cases. The paper does not quantify this error rate or provide guidance on how users should interpret the confidence of taxonomic assignments.\n\"Taxonomic misannotation is pervasive in NCBI GenBank and RefSeq: it has been estimated to affect 3.6% of prokaryotic genomes in GenBank and approximately 1% of its curated subset RefSeq... NCBI reported that they were flagging 75 genome submissions per month for review based on unexpected taxonomic annotation.\" [[5]](#citation-5)\nThis systematic review documents that taxonomic misannotation affects approximately 3.6% of prokaryotic records in GenBank. The microbeMASST database contains 60,781 files with taxonomic metadata largely derived from user submissions without genetic verification. Applying the 3.6% error rate suggests approximately 2,188 files may have incorrect taxonomic assignments. Since the tool's outputs include detailed taxonomic trees showing which organisms produce specific metabolites, these errors would directly mislead researchers about metabolite provenance.\n\nReferences:\n[5] [Ten common issues with reference sequence databases and how to mitigate them, PMC10978663](https://pmc.ncbi.nlm.nih.gov/articles/PMC10978663/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|53|GPT|1", "source": "prb", "split": "test", "paper_id": "prb53", "comment": "This paper overstates the validity of linking MS/MS spectra to specific microbial producers because the reference taxonomy is sometimes missing, generalized, or approximated, and the pipeline explicitly acknowledges that specimen identity cannot be verified genetically; this undermines the central producer-mapping claim in the Abstract and Methods.\n\n“Leveraging a curated database of >60,000 microbial monocultures, users can search known and unknown MS/MS spectra and link them to their respective microbial producers via MS/MS fragmentation patterns.”\nThis statement frames the tool’s output as linking spectra to their “respective microbial producers,” which implies a producer-level ground truth relationship rather than a metadata-level association. In practice, MS/MS matching against a repository of monoculture files can only inherit whatever organism labeling those files carry, and that labeling quality varies widely across contributed datasets. The manuscript later documents that it sometimes cannot assign a specific organism and may fall back to broad labels (e.g., “bacteria”/“fungi”). It also states that it may substitute a “closest taxon” when an NCBI ID is unavailable, which changes the claim from producer attribution to approximate taxonomic contextualization. Because this producer linkage is central to the paper’s stated contribution, the lack of verifiable organism identity is a publication-limiting validity gap.\n“Only monocultures were included in this search tool to unequivocally associate the production of the detected metabolites to each specific taxon.”\nThe paper uses “unequivocally” to justify monocultures as sufficient for attributing metabolites to taxa, but monoculture status alone does not guarantee correct taxon identity or exclude mislabeling/contamination. The same Methods section later reports that metadata harmonization was challenging and that organism names/IDs required manual curation and substitution, which directly contradicts “unequivocal” association. In addition, the manuscript retains blanks/QCs to “provide information on possible contaminants,” indicating that non-biological sources can contribute MS/MS spectra even within the curated corpus. In mass spectrometry-based metabolomics, unequivocal producer attribution typically requires stronger provenance (e.g., validated strain identity, controlled culturing, and/or orthogonal confirmation), not only monoculture labeling. As written, the claim risks readers treating taxon assignments as more definitive than the underlying evidence supports.\n“When metadata was not available and multiple species of bacteria or fungi were present in the same dataset, samples were generically classified as bacteria or fungi.”\nGeneric classification at the kingdom-level (or similarly broad categories) eliminates the ability to claim organism-specific producer mapping for those files. This practice can propagate ambiguous labels into the taxonomic tree, thereby inflating apparent producer breadth or creating misleading “hits” at higher ranks. It also makes downstream interpretation dependent on how much of the database falls into such generic bins, which the paper does not quantify in the main text. In a tool whose key value proposition is taxonomically informative mapping, a substantial fraction of non-resolved labels would materially affect conclusions about “respective microbial producers.” Importantly, this is not a minor metadata issue: it changes the inferential granularity of the primary output. Readers need a clear accounting of how often this occurs and how results are affected.\n“If the taxonomic name was not found in NCBI, most likely because it was not deposited yet, the NCBI of the closest taxon was retrieved and used.”\nSubstituting the “closest taxon” introduces systematic misclassification risk, especially at fine ranks (strain/species) where metabolite production can be highly lineage- and even strain-specific. This decision can make a spectrum appear associated with a well-known species/genus even when the actual isolate is a distinct, newly described taxon, thereby biasing producer inference toward known taxa. While this may be reasonable for navigation in a taxonomy tree, it is incompatible with strong claims of producer attribution. The manuscript does not describe criteria for “closest” (e.g., based on phylogeny, nomenclature similarity, depositor intent), nor does it estimate error introduced by these substitutions. In common microbial informatics practice, taxonomic assignment is ideally grounded in sequence-based identification rather than name matching alone.\n“Specimen assignment prior to metabolomic analysis can not be checked by microbeMASST. The majority of the deposited data do not have associated genetic information and even if available, it was not used to build taxonomic tree. Thus, specimen mis-identification is possible.”\nThis explicit limitation directly contradicts earlier language that monocultures allow “unequivocal” taxon attribution and should temper claims about producer mapping throughout the paper. If specimen identity can be wrong and genetic information is not used even when available, then taxon labels are not robust ground truth for biological producer inference. This is particularly consequential because the system aggregates matches up the taxonomic lineage, so any mislabeling can propagate to multiple nodes. The paper does not quantify how misidentification risk is managed (e.g., required evidence for manual curation, audit trails, confidence scoring). Without such controls, producer-level conclusions derived from these labels are not reliable. At minimum, stronger wording and quantitative validation of taxon label accuracy are needed.\n“The 16S rRNA subunit is considered as the universal target for bacterial identification from DNA with the aid of sequencing.” ([7](https://pubmed.ncbi.nlm.nih.gov/28718274/))\nThis sentence summarizes a widely used baseline practice for confirming bacterial identity using genetic data, highlighting a methodological gap in microbeMASST’s reliance on community-provided names/NCBI IDs. The paper acknowledges that genetic information is mostly absent and not used even when present, which falls short of common authentication workflows when organism identity is central to the claim. In a producer-attribution tool, lack of sequence-based confirmation means the “producer” may not be the organism actually measured, particularly across thousands of contributed monocultures. This matters because metabolite production is often strain-dependent, and misidentification can lead to incorrect biological narratives or wasted follow-up experiments. The citation does not imply microbeMASST must perform sequencing, but it does show that the manuscript’s “unequivocal” framing is inconsistent with standard identification rigor. Consequently, the paper’s core validity claim about mapping to producers is weakened.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|53|GPT|2", "source": "prb", "split": "test", "paper_id": "prb53", "comment": "This paper’s conclusion that many spectra are “putative microbial” and that microbial metabolites “reach and influence distant organs” is not robust because the described filtering (including removal of spectra matching human cell lines) and cross-dataset overlap checks do not distinguish microbial biosynthesis from host–microbe co-metabolism, diet-derived compounds, or host responses to colonization.\n\n“We extracted 10,047 consensus MS/MS spectra uniquely present in SPF mice and queried them with microbeMASST. A total of 3,262 MS/MS spectra were found to have a microbial match. Of these, 837 were also found in human cell lines and for this reason were removed from further analysis.”\nThe workflow equates a match to a monoculture spectrum with “microbial” origin, then uses presence in human cell lines as a proxy for host origin, but neither step is a definitive causal test. A spectrum can match microbial monocultures due to shared metabolites (e.g., dietary components, media contaminants, conserved biochemistry) or because the same molecular family is produced across many contexts. Conversely, absence from a limited set of cell line cultures does not imply a molecule cannot be host-derived in vivo, since tissue metabolism, microbiota-induced host pathways, and diet-dependent host products are not represented by cell lines. The paper also notes elsewhere that blanks/QCs are retained to flag contaminants, implying that non-biological matches are plausible and should be systematically controlled rather than filtered only by cell-line presence. Without orthogonal validation (e.g., controlled gnotobiotic colonization with known strains, isotope tracing, or targeted confirmation), the “putative microbial” label is not sufficiently supported for strong biological conclusions. As a result, downstream interpretations built on this set (including human dissemination claims) are not reliable.\n“These findings support the concept that a significant number of microbial metabolites reach and influence distant organs in the human body35.”\nThis is a strong mechanistic interpretation (“reach and influence”) that requires demonstrating both microbial origin and transport to organs, yet the presented evidence primarily shows spectral matches in public datasets and correlations with colonization status. Spectral presence in blood, brain, or other organs (via repository searches) can arise from multiple sources, including dietary intake, pharmaceuticals, host metabolism, or environmental exposure, and does not on its own establish microbial synthesis. Even if colonization is necessary for the signal, that could reflect host metabolic regulation by microbes rather than direct microbial production of the detected molecule. The manuscript itself lists an alternative hypothesis (“microorganisms can also selectively stimulate the production of host metabolites”), underscoring that the current evidence does not resolve causality. In contemporary host–microbiome metabolomics, causal attribution typically requires experimental designs that directly trace microbial versus host production and account for confounders (diet, exposure, analytical variability). The current analysis does not meet that bar, making the conclusion overstated.\n“The mammalian gut microbiota interact extensively with the host through metabolic exchange and co-metabolism of substrates.” ([3](https://pubmed.ncbi.nlm.nih.gov/15821725/))\nThis statement highlights a central reason why binary classification of metabolites as purely “microbial” versus “host” is often invalid in vivo. Because many small molecules are co-metabolites shaped by both microbial and host enzymes, identifying a spectrum as “microbial” based on monoculture matches and absence from cell lines is not sufficient to establish origin. The paper’s own discussion that some metabolites “traditionally considered to be non-microbial” might be microbially produced or host-stimulated aligns with this complexity but does not provide a method to disambiguate it. In such settings, robust conclusions typically require additional evidence (e.g., isotope labeling, defined consortia, enzymatic knockouts) beyond repository matching. Therefore, the external literature supports that the manuscript’s inference framework is underdetermined. This directly weakens the reliability of the paper’s key biological interpretation claims.\n“Such metabolome-metabolome interactions are poorly understood, but might be implicated in the aetiology of many human diseases.” ([3](https://pubmed.ncbi.nlm.nih.gov/15821725/))\nThis sentence reinforces that interpreting metabolomic differences across colonization states is intrinsically challenging and easily confounded by indirect effects. The manuscript’s approach (repository matching + cell-line filtering + antibiotic overlap) does not explicitly model these indirect effects, nor does it quantify uncertainty about origin assignments. When interactions are “poorly understood,” stronger methodological safeguards are needed before asserting organ-level influence in humans. The paper’s human-dataset search is particularly vulnerable because it aggregates heterogeneous studies with varying sample handling, instrument settings, and metadata quality, any of which can affect MS/MS detectability. As a consequence, evidence of “presence” across many human datasets cannot be cleanly translated into claims about microbial metabolite dissemination. The literature therefore supports a more cautious interpretation than the manuscript currently presents.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|53|GPT|3", "source": "prb", "split": "test", "paper_id": "prb53", "comment": "This paper’s matching methodology risks high false positive rates because it uses permissive defaults (minimum of three matched fragment ions) at very large search scale and does not report any false discovery rate estimation, decoy strategy, or statistical calibration; this undermines validity of reported matches and downstream taxonomic/biological conclusions.\n\n“As of June 2023, microbeMASST includes 60,781 liquid chromatography (LC)-MS/MS files, comprising >100 million MS/MS spectra…”\nSearching a query spectrum against a repository on the order of 10^8 spectra is a classic multiple-comparisons setting where even low per-comparison error rates can generate substantial absolute numbers of false matches. In such contexts, reporting only heuristic thresholds (cosine score and matched peaks) without an accompanying error model leaves readers unable to gauge reliability. This is especially important because microbeMASST aggregates results up the taxonomic lineage and presents distributions across taxa, which can amplify the interpretive impact of spurious matches. The manuscript does not provide an estimate of how often false positives occur at the chosen settings, nor how results change under stricter thresholds. Without statistical calibration, matches may reflect chance alignments or systematic artifacts rather than shared molecular identity. Therefore, the scale of the search makes statistical control a central requirement, not an optional refinement.\n“Searches are customizable and default settings are the following: precursor and fragment ion mass tolerances = 0.05, minimum cosine score threshold = 0.7, minimum number of matching fragment ions = 3, and analog search = False.”\nA minimum of three matched fragment ions is unusually permissive for asserting confident spectral similarity, particularly in untargeted metabolomics where many spectra are sparse and fragment peaks can recur across unrelated compounds. Combined with a cosine threshold of 0.7 and relatively wide tolerances (0.05 Da), these defaults can admit ambiguous or noisy matches. The manuscript does not justify why three matching ions is adequate at repository scale, nor does it provide sensitivity analyses showing stability of conclusions when increasing the minimum matched peaks. The paper also does not define how these defaults were selected (empirical calibration, benchmarking on held-out truth sets, or conventional GNPS defaults). Because the central product of microbeMASST is match-driven taxonomic mapping, match-quality choices directly affect validity. As presented, the defaults are not sufficiently defended for high-stakes biological interpretation.\n“Generally, the default of cosine of 0.7 and 6 minimum matches peaks reduces the number of false positive alignments tremendously.” ([1](https://ccms-ucsd.github.io/GNPSDocumentation/massspecbackground/networkingtheory/))\nThis GNPS documentation explicitly motivates using a higher minimum matched peaks (6) with cosine 0.7 to control false positives in spectral alignment. MicrobeMASST’s stated default of three matched fragment ions is half of that commonly recommended baseline, which would be expected to increase false matches, especially when searching very large repositories. The discrepancy matters because the manuscript treats matches as evidence of microbial origin/producer association and uses them for downstream biological narratives. If default settings are more permissive than standard practice, the paper should provide compensating evidence (e.g., FDR estimates, targeted validation, or benchmarking) demonstrating that precision remains acceptable. The manuscript does not provide such quantitative validation. Therefore, the external guideline directly supports the criticism that match criteria are insufficiently conservative.\n“While various spectrum-spectrum match scores exist, the field lacks statistical methods for estimating the false discovery rates (FDR) of these annotations.” ([2](https://pmc.ncbi.nlm.nih.gov/articles/PMC5684233/))\nThis statement from the spectral-matching literature emphasizes that heuristic scoring alone is not enough to interpret annotation reliability, particularly across large analyses. MicrobeMASST operates in exactly the large-scale regime where FDR control is most needed, yet the manuscript does not incorporate any FDR estimation or uncertainty quantification for match lists. The paper also does not discuss how often matches might be expected by chance under its defaults, or how database size affects error rates. Without FDR or similar calibration, downstream counts such as “3,262 MS/MS spectra were found to have a microbial match” are difficult to interpret as evidence rather than as threshold artifacts. The critique is not that FDR estimation is trivial, but that at this scale it is standard to at least provide some statistical control or sensitivity analysis. The absence of this undermines confidence in the reported results.\n“By adjusting the scoring parameters and thresholds, the number of annotations rose, on average, by +139% (ranging from −92 up to +5705%) when compared with a default parameter set available at GNPS.” ([2](https://pmc.ncbi.nlm.nih.gov/articles/PMC5684233/))\nThis sentence underscores that spectral-matching outcomes are highly sensitive to parameter settings and that defaults can be far from optimal or stable across datasets. MicrobeMASST presents many quantitative outcomes (counts of “microbial matches,” overlaps across studies, distributions across phyla) without exploring how these outcomes vary under plausible alternative thresholds. Given that microbeMASST also introduces nonstandard defaults (e.g., three matched peaks), this sensitivity becomes a central threat to conclusion robustness. The cited work argues for dataset-specific calibration, which the manuscript does not perform for its showcased biological analyses. Without such calibration, it is unclear whether the reported numbers reflect biological signal or parameter choice. Thus, the external literature supports the need for more rigorous statistical treatment than what is presented.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|53|GPT|4", "source": "prb", "split": "test", "paper_id": "prb53", "comment": "This paper does not provide a reproducible computational pathway to regenerate reported results because the core search depends on an external Fast Search API over continuously updated public repositories and the accompanying code suggests intermittent failures and silent exception handling, making outputs potentially non-deterministic across time and runs.\n\n“Fast searches are based on indexing all the MS/MS spectra present in GNPS/MassIVE according to the mass and intensity of their precursor ions and then restricting the search to only a set of relevant spectra…”\nIndexing “all” spectra in a public repository implies that the search corpus is not fixed: GNPS/MassIVE grows continuously and may also change due to reprocessing or metadata updates. The manuscript does not specify a frozen snapshot (e.g., a dated index build, DOI, or checksum) for the Fast Search index used to generate the paper’s quantitative results. This omission is consequential because even small changes in the indexed corpus can change match sets, counts, and apparent taxonomic distributions, especially for borderline matches near the threshold. The paper’s own “As of June 2023” phrasing indicates temporal dependence, but it does not provide a mechanism for future readers to reproduce that June-2023 state. In computational metabolomics, reproducibility typically requires pinning both software versions and data snapshots. Without that, the reported results are not regenerable in a principled way.\n“Make sure to run jobs.py a couple of times, until no new output is generated by having the option: skip_existing=True. Due to the Fast Search API some of the entries will fail. Nevertheless sequent re-runs should catch all the possible matches.”\nThis note in the provided code repository indicates that batch search outcomes may depend on transient API failures rather than deterministic computation. If “some of the entries will fail,” then a single run does not reliably produce a complete match set, and repeated runs are recommended as a workaround rather than a controlled retry strategy with reporting. This fragility is a serious reproducibility issue because it can lead to missing matches, inconsistent downstream counts, and potentially biased taxonomic summaries (e.g., failures may correlate with query complexity or server state). The manuscript does not describe how such failures were tracked or corrected in the analyses presented. Moreover, “until no new output is generated” is not a quantitative stopping criterion and does not provide an auditable record of completeness. Therefore, the code evidence suggests the results pipeline is not robust enough to support the strength of the paper’s conclusions.\n```python\n# /preprint/code/code/jobs.py\nfor file, out_file in files:\n    try:\n        logger.info(\"Starting new job for input: {}\".format(file))\n        ...\n        masst_batch_client.run_on_usi_list_or_mgf_file(\n            ...,\n            skip_existing=True,\n            ...,\n        )\n    except:\n        pass\n# exit with OK\nsys.exit(0)\n```\nThe batch driver suppresses all exceptions (`except: pass`) and then exits successfully (`sys.exit(0)`), which can silently hide partial failures and create outputs that look complete but are not. In a results-generating pipeline, silent failure is a major threat to both reproducibility and validity because it prevents users (and the authors) from knowing which queries failed and why. This is especially problematic when combined with an external API that the README states can fail for some entries. The paper reports concrete numbers (e.g., 3,262 matches; 2,425 filtered spectra; 512 antibiotic-sensitive spectra) that would be sensitive to silent query dropouts. Without explicit failure reporting and deterministic rerun logic, independent reproduction of these counts is unreliable. This is not a minor software engineering nit: it directly affects whether the manuscript’s reported results can be trusted.\n```python\n# /preprint/code/code/masst_utils.py\nURL = \"https://fasst.gnps2.org/search\"\nclass DataBase(Enum):\n    metabolomicspanrepo_index_nightly = auto()  # all gnps data\n...\nsearch_api_response = requests.post(URL, data=params, timeout=300)\n```\nThe code hard-codes a remote endpoint and references a “nightly” index, implying that the effective database changes over time. This means that rerunning the same analysis at a later date may produce different match sets even with identical parameters and input spectra. The manuscript does not specify which index build was used for the reported figures (e.g., nightly vs a dated snapshot) nor does it provide a mechanism to reconstruct historical indices. In large public-repository search tools, versioned indices and explicit provenance are commonly used to support reproducibility and benchmarking. Without this, the paper’s quantitative results become a moving target tied to an evolving service. This weakens the manuscript’s methodological transparency and long-term scientific utility.\n“We also introduce the concept of 'living data' through continuous reanalysis of deposited data.” ([6](https://pubmed.ncbi.nlm.nih.gov/27504778/))\nThis GNPS framing is scientifically valuable but highlights the reproducibility challenge: if deposited data are continuously reanalyzed, downstream search results are inherently time-dependent. MicrobeMASST builds on this ecosystem and should therefore provide stronger versioning/provenance to allow readers to reproduce the state used for the paper’s analyses. The manuscript does not provide a date-stamped index identifier or archived result bundles sufficient to regenerate the search outputs from scratch. In such “living data” infrastructures, best practice is to accompany published analyses with frozen snapshots or persistent identifiers for the exact computational environment and data state. Without these, the work is difficult to evaluate or build upon quantitatively. Thus, the external literature reinforces that the paper should treat reproducibility as a first-class design requirement.\n“Reproducibility has the potential to serve as a minimum standard for judging scientific claims when full independent replication of a study is not possible.” ([5](https://pubmed.ncbi.nlm.nih.gov/22144613/))\nThis sentence captures why the reproducibility weaknesses above are not merely technicalities: for complex, large-scale repository mining, independent experimental replication is often infeasible, making computational reproducibility the key evaluative standard. MicrobeMASST’s dependence on a dynamic remote index and a failure-prone API means that readers cannot reliably reproduce the analyses that support the paper’s biological claims. The manuscript provides links and code pointers, but does not ensure determinism or complete provenance for the results shown. This makes it hard to judge whether reported match counts and distributions are stable findings or artifacts of a particular transient system state. The paper could mitigate this by archiving the exact query inputs, parameters, index version, and outputs used for each figure. As written, it falls short of the minimum standard articulated in the cited reproducibility literature.\n“There is an urgent need to improve the infrastructure supporting the reuse of scholarly data.” ([4](https://pubmed.ncbi.nlm.nih.gov/26978244/))\nMicrobeMASST is positioned as infrastructure for reusing public mass spectrometry data, so its published form should meet strong reuse and reproducibility expectations. The reliance on a continuously updated corpus and an external service without pinned versions limits downstream reuse because results cannot be regenerated or compared fairly across time. The manuscript would be strengthened by explicitly adopting reuse-oriented practices such as persistent identifiers for database snapshots, parameter provenance, and auditable logs of failed queries. Without these, users cannot confidently reuse the tool outputs for meta-analyses or longitudinal comparisons. The cited FAIR principles emphasize reusability as a design goal, not an afterthought. Therefore, the paper’s current reproducibility gaps materially impact its methodological contribution.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|53|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb53", "comment": "The utility of microbeMASST is severely limited by the predominant use of positive ionization mode in the reference database, which excludes a vast array of microbial metabolites that ionize preferentially in negative mode.\n\n\"The majority of the data deposited in public repositories, GNPS included, and used in microbeMASST were acquired using positive ionization mode, which limits the observation of molecules that cannot be ionized in positive mode.\"\nThe authors admit this limitation, but it is a critical flaw for a tool aiming to be a comprehensive resource for microbial metabolomics. Many key microbial metabolite classes, such as organic acids, fatty acids, and certain lipids, are best detected in negative ionization mode [1]. By relying on a database that systematically underrepresents these molecules, the tool provides a skewed view of microbial metabolism.\n\"This means that certain metabolites may be underrepresented or not detected at all.\"\nThis underrepresentation is not just a minor gap but a systematic bias that affects the biological conclusions users can draw. For example, a user searching for a negative-ionizing metabolite will likely get a false negative result, leading them to incorrectly conclude the molecule is not of microbial origin, simply because the reference data is biased.\n\nReferences:\n[1] Vinaixa, M. et al. Mass spectrometry in metabolomics: latest advances and future perspectives. TrAC Trends in Analytical Chemistry 82, 21–38 (2016).", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|53|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb53", "comment": "The paper does not address the estimation or control of False Discovery Rate (FDR) for the spectral matching, which is critical given the large search space and the potential for random high-scoring matches.\n\n\"Search parameters, such as parent ion and fragment ions tolerances, cosine threshold, and minimum matching peaks can be modified.\"\nThe method relies on raw cosine similarity scores and minimum matched peaks to define a match. However, it is well-established in metabolomics that cosine scores alone are insufficient to control the False Discovery Rate, especially when searching against large databases [2]. Without an FDR estimation (e.g., using a decoy database or probability-based scoring), users have no measure of confidence in the reported matches, which is standard practice in mass spectrometry-based omics [3].\n\"Because of this, search results are returned within seconds as opposed to 20 min per search...\"\nWhile the \"Fast Search Tool\" improves speed, the paper does not discuss whether this speed comes at the cost of statistical rigor regarding false positives. In proteomics, from which the Fast Search Tool was adapted [3], FDR control is mandatory. Its absence here raises concerns about the reliability of the \"microbial matches\" reported, particularly for spectra with lower signal-to-noise ratios.\n\nReferences:\n[2] Scheubert, K. et al. Significance estimation for large scale metabolomics annotations by spectral matching. Nat. Commun. 8, 1494 (2017).\n[3] Batsoyol, N. et al. P-massive: a real-time search engine for a multi-terabyte mass spectrometry database. In Proceedings of the International Conference on High Performance Computing, Networking, Storage and Analysis 1–15 (IEEE Press, 2022).", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|53|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb53", "comment": "The construction of the reference database is not reproducible, as the code for curating and filtering the >60,000 LC-MS/MS files into the final metadata table is not provided.\n\n\"The microbeMASST reference database of monocultures has been generated through years of community contributions and metadata curation...\"\nThe paper describes a massive curation effort but does not provide the scripts or protocols used to generate the final `microbe_masst_table.csv` from the raw community data. The provided code repository contains scripts that start by reading the already-processed CSV file (e.g., `microbemasst_tree_generator.R` starts with `data <- read_csv(\"microbe_masst_table.csv\")`).\n\"microbemasst_tree_generator.R\"\n  ```r\n  data <- read_csv(\"microbe_masst_table.csv\")\n  # Extract unique NCBI IDs\n  unique_ncbi <- data %>% distinct(Taxa_NCBI) ...\n  ```\nThis code block demonstrates that the workflow provided begins *after* the critical database creation step. Without the curation scripts, it is impossible for other researchers to reproduce the database, understand the inclusion/exclusion criteria for specific files, or update the database with new data in a consistent manner.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|53|Gemini|5", "source": "prb", "split": "test", "paper_id": "prb53", "comment": "The tool's reliance on community-contributed metadata without a robust, automated verification mechanism introduces a significant risk of error propagation and database contamination.\n\n\"Specimen assignment prior to metabolomic analysis can not be checked by microbeMASST. The majority of the deposited data do not have associated genetic information and even if available, it was not used to build taxonomic tree. Thus, specimen mis-identification is possible.\"\nThe authors explicitly acknowledge this vulnerability. In a \"taxonomically-informed\" tool, the accuracy of the taxonomy is paramount. Relying on user-provided metadata without genomic validation means that a single misidentified culture or contaminated sample can propagate errors to all future searches.\n\"microbeMASST is a community-sourced tool that works within the GNPS ecosystem.\"\nWhile community sourcing is powerful, it requires strict quality control. The paper does not describe any automated QC steps to flag potential metadata mismatches (e.g., checking if a \"Streptomyces\" file actually contains characteristic Streptomyces metabolites). This lack of QC compromises the reliability of the \"microbial producer\" links generated by the tool.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|53|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb53", "comment": "While a few examples were described and the data interpretation was given, the limitation of the tool and the caution of data interpretation based on the information provided by the database should be highlighted in these examples rather than in Method, e.g. MS/MS match does not guarantee confirmation of a metabolite, signals that are not present in the microorganism or human cell line culture do not necessarily indicate they cannot be produced by them, caution should be paid when claiming the sole origins of the metabolites. Specifically, “Based on literature information, the list of annotated MS/MS spectra contained a small number of metabolites traditionally considered to be non-microbial in origin.” Some examples from this small number of metabolites should be given here. It is unclear if this list is the new finding from the tool. If so, examples of metabolites given below (serotonin, γ-aminobutyric acid (GABA), and the glycocholic acid) are not supportive to the finding since these metabolite are known to be produced by both the mammalian host and bacteria. “… with microorganisms often being the primary producers of these metabolites in the gut.” References should be cited to indicate microorganisms are the primary producers rather than the mammalian host. What does the ‘gut’ refer to here, the gut lumen or gut tissue?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|53|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb53", "comment": "In order for the microbeMASST to be useful in metabolomics studies, it would be important that the tool could annotate datasets from metabolomics studies. This is indeed possible through batch processing, but this is only briefly mentioned in the supplement, referring to Python code that does not seem to be available.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|53|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb53", "comment": "Is it foreseen that microbeMASST could be integrated with the data processing softwares, e.g., MZmine? There is no mention how the tool could be used as part of the integrated data processing pipeline.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|53|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb53", "comment": "With regards to the murine study used as an example (Fig. 2), the study is properly referenced and there is sufficient detail in the supplement. However, in main manuscript, it would be useful to know where the spectra are coming from (specific tissues, biofluids).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|53|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb53", "comment": "Some of the descriptions of numbers of LC-MS/MS files and MS/MS spectra are a little confusing and could be clarified. For example when it is mentioned “each MS/MS query is searched against the public MS/MS reference library of GNPS, this wasn’t quite clear whether the GNPS library vs. the microbeMASST libraries contain different data or a subset of just microbial data?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|53|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb53", "comment": "There is also some assumption of prior knowledge of MASST and GNPS for the reader. It is written that microbeMASST works within GNPS, therefore how does using the GNPS system to search for an entry, differ from using the microbeMASST system, is it the link to the taxa? It also seems that the advance from MASST to microbeMASST is the speed and taxonomy link, is the datasource the same? Perhaps this could be clarified.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|53|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb53", "comment": "For the interface could the authors explain more what a USI refers to and how it was constructed, I believe this is a term introduced by the proteomics field 2 years ago but not commonly used in metabolomics? Is this specific to GNPS or is it used outside of this software? Also what do the inputs and outputs mean on the system, and are there recommended thresholds for matching based on the mass accuracy of the analysis performed by the contributors? without apriori knowledge. For example for charge it seems this is the number of charges vs a negative or positive charge. It seems like ESI mode might be important as well for generating a match, but it doesn’t appear this is an input anywhere?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|53|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb53", "comment": "When there is more than one metabolome curated for a given microbe, I see that there are available samples and matching samples listed. If the MS/MS spectrum that one enters matches to 50% of that microbe (represented as the pie chart), is that a complete match to half of the available samples? Or are X number of peaks matched similarly in that half of the samples. This could be the explanation for the taxa matches tab but it isn’t clear – could it also be explained what all the outputs mean on this tab as well?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|53|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb53", "comment": "In general the font sizes are too small on the figures when reading the paper at 100% zoom.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Claude|1", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "The paper draws sweeping conclusions about the clinical utility and superiority of real-time nanopore genomics over established diagnostic methods based on a single patient case, which is fundamentally insufficient to validate any clinical diagnostic approach.\n\n\"We here showcase the potential power of in situ real-time genomics in the clinical setting through the example of a Klebsiella pneumoniae infection that harbors a newly discovered antibiotic resistance gene in low abundance.\"\nThe authors explicitly acknowledge their study is based on a single clinical case (\"through the example of\"), yet they proceed to make broad claims about the technology's potential to improve clinical practice. Standard practice for validating clinical diagnostic methods requires prospective studies with adequately powered sample sizes to detect meaningful differences in clinical outcomes. A single case study cannot control for confounding variables, account for natural variation in bacterial populations, or provide the statistical power necessary to draw reliable conclusions about diagnostic superiority.\n\"The fast, adaptive, and in situ nature of antibiotic resistance profiling by nanopore sequencing would have surpassed current clinical practice in accurately informing clinical management.\"\nThis claim that nanopore sequencing \"would have surpassed current clinical practice\" represents a strong assertion about diagnostic superiority that cannot be substantiated by a single retrospective case. The conditional framing (\"would have\") acknowledges this was not demonstrated in practice but is stated as if it were a validated finding. Clinical validation studies for diagnostic tests typically require systematic comparison across multiple patients with varying presentations, as recommended by regulatory bodies and clinical research guidelines.\n\"Given the expected high rate of antibiotic resistance emergence in the future, the demonstrated insufficiency of clinically established resistance detection approaches to accurately assess complex infections could pose a significant threat to efficient antibiotic treatment.\"\nThe authors characterize their single case as having \"demonstrated\" the insufficiency of established methods, implying broad conclusions about standard-of-care diagnostics from n=1. As established in clinical research methodology, demonstrating that a diagnostic method is insufficient requires systematic comparison across representative patient populations, not a single example where an unusual resistance pattern was missed.\n\"To establish power and sample sizes for typical microbiome study scenarios... Implementation of these methods will improve the quality of human or animal microbiome studies, enabling reliable conclusions that will generalize beyond the study sample.\" [[1]](#citation-list)\nThis guidance from clinical genomics research explicitly states that proper sample size calculation is essential for conclusions to \"generalize beyond the study sample.\" The reviewed paper's conclusions about clinical utility from a single case cannot meet this standard of generalizability that is expected in the field.\n\nReferences:\n[1] [Dallow J, et al. \"Power and sample size calculation for microbiome studies.\" Journal of Clinical Investigation (2022)](https://www.sciencedirect.com/science/article/pii/S1933021922017366)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Claude|2", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "Despite the paper's title emphasizing \"real-time genomics,\" the analysis was performed retrospectively on stored samples after the patient had passed away, fundamentally undermining claims about real-time clinical utility.\n\n\"We simulated the retrospective clinical application of real-time genomics for antibiotic resistance prediction for this infection case as follows\"\nThe authors explicitly describe their approach as a \"retrospective clinical application\" that was \"simulated,\" not actually performed in real-time during patient care. This is a critical distinction because the challenges of implementing genomic diagnostics in real clinical workflows—including sample processing time, result interpretation under time pressure, and integration with clinical decision-making—cannot be assessed in a retrospective simulation. The title \"Detection of hidden antibiotic resistance through real-time genomics\" suggests prospective detection, but the methodology reveals this was purely retrospective.\n\"After completion of the phenotypic processing, the isolates were stored at -80°C.\"\nThis methodological detail confirms that the samples used for nanopore sequencing were frozen archival specimens, not fresh clinical samples processed in real-time. Working with frozen isolates eliminates the practical challenges of fresh sample processing, DNA extraction quality variability, and the time constraints of actual clinical workflows. The storage and subsequent thawing process may also affect DNA quality and potentially alter the representation of different plasmid populations.\n\"We used real-time genomics to sequence DNA from the pre- and post-CAZ-AVI treatment isolates using the portable nanopore sequencing device Mk1b. Both isolates were sequenced for 15 hours, and the first isolate was sequenced for another 20 hours to simulate the potential adaptive sequencing in the clinical setting.\"\nThe 15-20 hour sequencing times described, while feasible in a research setting, were not evaluated within the actual clinical workflow constraints where treatment decisions need to be made rapidly. The study design allows for optimization and repeated analysis that would not be available in true real-time clinical deployment. Furthermore, the additional 20-hour sequencing run to detect more KPC-14 copies represents a retrospective optimization that could not have been anticipated during actual patient care.\n\"Retrospective and non-randomized real-world studies are subject to bias and confounding factors, problems that are controlled for in randomized blinded trials... This, together with heterogeneity in terms of clinical practice and associated documentation, may lead to a reduced capability of the study to answer the research question.\" [[2]](#citation-list)\nThis established guidance on real-world clinical studies highlights that retrospective designs are inherently subject to biases that prospective studies can control. The reviewed paper's retrospective simulation cannot account for the practical challenges that would arise during actual real-time implementation in a clinical microbiology laboratory.\n\nReferences:\n[2] [Interpretation and Impact of Real-World Clinical Data for the Future of Healthcare. PMC (2018)](https://pmc.ncbi.nlm.nih.gov/articles/PMC6223979/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Claude|3", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "The paper does not sufficiently address the documented variability and often limited accuracy of nanopore sequencing-based antibiotic resistance prediction compared to phenotypic testing, which is critical context for interpreting the clinical significance of their findings.\n\n\"Additionally, we chose to only include respective KPC-2 and KPC-14 resistance genes with detection accuracies above 90% to minimise the chances of false positive resistance gene detection.\"\nWhile the authors apply a 90% accuracy threshold for gene detection, they do not discuss the more fundamental issue of genotype-phenotype concordance—whether detecting a resistance gene accurately predicts the actual phenotypic resistance behavior. The presence of a gene does not always equate to phenotypic expression, particularly for resistance genes that may require specific expression conditions, promoter elements, or additional regulatory factors.\n\"Phenotypic resistance was observed in 28 cases (pink squares in Figure 4). AMR prediction was accurate in 16 cases (57.14%) with the command line approach and in 9 cases (32.14%) using EPI2ME... A comparison between the two pipelines showed good concordance in 26 cases (62.5%), which dropped down to 6 cases (7.4%) when comparing genotyping to phenotypic results.\" [[3]](#citation-list)\nThis recent study evaluating nanopore-based AMR prediction using EPI2ME—the same analysis platform used in the reviewed paper—found only 32.14% accuracy in predicting phenotypic resistance when using EPI2ME. This substantial discordance between genotype detection and phenotype prediction represents a significant limitation that the reviewed paper does not acknowledge. The fact that genotype-phenotype agreement was as low as 7.4% for some antibiotic classes raises serious concerns about the clinical reliability of such predictions.\n\"However, concerns remain about the accuracy of real-time genomics for phenotypic antibiotic resistance prediction in comparison to established diagnostic approaches.\"\nThe authors acknowledge these concerns in their introduction but do not provide systematic data addressing them. Instead, their conclusion that nanopore sequencing \"outperform[s] established diagnostics in accuracy\" appears to be based solely on the single case where the KPC-14 gene was detected, without addressing the broader context of variable accuracy rates documented in the literature.\n\"This meta-analysis also demonstrates that nanopore sequencing achieves a pooled sensitivity ranging from 77.99 to 93.66% and pooled specificity between 94.84% and 99.47% in diagnosing drug-resistant (DR)-MTB, depending on the specific drug tested.\" [[4]](#citation-list)\nMeta-analyses of nanopore sequencing accuracy show that performance varies substantially depending on the drug and resistance mechanism being tested. The reviewed paper does not position their findings within this context of variable accuracy, instead presenting their single case as evidence of superior diagnostic capability.\n\nReferences:\n[3] [Nanopore Sequencing-Driven Mapping of Antimicrobial Resistance Genes. PMC (2025)](https://pmc.ncbi.nlm.nih.gov/articles/PMC12382671/)\n[4] [Diagnostic accuracy of nanopore sequencing for detecting drug-resistant tuberculosis. Nature Scientific Reports (2025)](https://www.nature.com/articles/s41598-025-90089-x)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Claude|4", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "The paper identifies low-abundance KPC-14 copies but provides no framework or threshold for when such detections should influence clinical decision-making, leaving the practical clinical applicability unclear.\n\n\"Our real-time genomics approach importantly also detected one copy of the KPC-14 resistance gene in the pre-treatment isolate; while this one copy would have been too little evidence to predict phenotypic CAZ-AVI resistance\"\nThe authors acknowledge that detecting one copy of KPC-14 was \"too little evidence\" to predict resistance, but they do not provide any threshold or criteria for when detection would be sufficient. This lack of defined thresholds is a significant gap because the clinical utility of any diagnostic test depends on actionable decision rules. Without establishing what number of resistance gene copies, what proportion relative to dominant variants, or what other criteria would warrant clinical action, the finding remains of unclear practical value.\n\"our simulation of the adaptive application of real-time genomics in the clinic showed us that less than 20 hours of additional sequencing would have resulted in the detection of four more highly accurate copies of KPC-14\"\nThe authors suggest that detecting 5 total KPC-14 copies (after additional sequencing) would constitute sufficient evidence, but this remains unstated as a formal threshold. In clinical practice, having 40 copies of KPC-2 alongside 5 copies of KPC-14 raises questions about what proportion would be clinically significant. The paper does not establish whether 5:40 (11%), 1:40 (2.4%), or some other ratio should trigger clinical concern or treatment modification.\n\"The second KPC-14 gene copy would have already been detected after two hours of additional sequencing and could have rapidly influenced antibiotic treatment through the early detection of CAZ-AVI resistance potential\"\nThe suggestion that two KPC-14 copies could \"have rapidly influenced antibiotic treatment\" contradicts the earlier statement that one copy was \"too little evidence.\" This creates ambiguity about the threshold for clinical action. Without prospective validation of decision thresholds, clinicians would have no guidance on how to interpret and act on such low-abundance gene detections.\n\"Heteroresistance, defined as the presence of a subpopulation of cells with a higher MIC than the dominant population, is a frequent phenotype in many pathogens... Due to the low frequency of resistant cells, heteroresistance may be neglected and undetected by standard antimicrobial susceptibility testing (AST)\" [[5]](#citation-list)\nThe phenomenon of heteroresistance—where minority resistant subpopulations exist within predominantly susceptible populations—is well-documented. However, detecting such subpopulations does not automatically mean clinical action is warranted, as these subpopulations may or may not expand under treatment. The reviewed paper does not address how clinicians should distinguish between clinically significant heteroresistance requiring treatment modification versus incidental detection of minor variants that may not affect treatment outcomes.\n\nReferences:\n[5] [Antibiotic Heteroresistance in Klebsiella pneumoniae. PMC (2022)](https://pmc.ncbi.nlm.nih.gov/articles/PMC8745652/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|GPT|1", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "This paper overstates clinical impact and superiority over standard diagnostics (Validity, Conclusions) based on a retrospective, simulated workflow rather than a prospective or real-time clinical deployment of the described nanopore pipeline.\n\n\"We here show that real-time genomics has the potential to improve clinical practice based on a multi-drug resistant Klebsiella pneumoniae bloodstream infection. In contrast to established diagnostics, real-time genomics can accurately identify complex antibiotic resistance patterns conferred through newly discovered low-abundance resistance genes, potentially significantly impacting clinical decision-making and patient outcome.\"\nThese sentences frame the work as demonstrating improved clinical practice and accurate resistance identification relative to standard diagnostics, which is a strong conclusion for a single-case report. The paper does not present a prospective clinical evaluation, a cohort, or any systematic comparison of diagnostic accuracy metrics (e.g., sensitivity/specificity) across multiple samples. The evidence provided later in the manuscript is explicitly described as a simulation on stored isolates, not an intervention that affected patient management. In clinical microbiology, claims about improving outcomes or decision-making typically require either prospective deployment, controlled comparisons, or at least a defined evaluation protocol and error analysis. Without such design elements, the conclusion reads as a hypothesis supported by a retrospective illustration rather than a demonstrated clinical improvement. This gap materially affects how the work should be interpreted (illustrative case study vs. validated diagnostic advance).\n\"We simulated the retrospective clinical application of real-time genomics for antibiotic resistance prediction for this infection case as follows:\"\nThis sentence explicitly limits the study to a retrospective simulation rather than a real-world, real-time diagnostic workflow used to guide therapy. A simulation can be useful for feasibility, but it cannot establish that the approach would have changed clinical decisions at the necessary timepoints, nor that it would have done so reliably under routine constraints. Because the main claims emphasize rapid, actionable predictions, a retrospective simulation is not sufficient evidence for superiority in clinical practice. The distinction matters because many practical failure modes (workflow delays, sample logistics, contamination controls, interpretability) only appear under prospective deployment. The paper does not provide an analysis of how the simulated timing aligns with clinical decision deadlines in this case. As a result, the manuscript’s causal language about clinical impact is not justified by the presented study design.\n\"The stored isolates were thawed and grown overnight at 37°C on BD® Columbia blood agar plates.\"\nThis described workflow step introduces an additional incubation period before sequencing that is incompatible with the paper’s framing of rapid, *in situ* decision support in this case study. Even if nanopore sequencing generates data soon after starting a run, the operational timeline here includes thawing and overnight growth, which can shift turnaround time by many hours. This weakens the implied comparison with clinical workflows on speed and actionability, since the manuscript does not quantify end-to-end time-to-result under the reported laboratory steps. In the clinical sequencing literature, turnaround time claims are typically anchored to a defined starting point (e.g., sample receipt) and include all preprocessing steps. By not reconciling this overnight culturing step with the claimed rapidity, the paper risks conflating technological potential with what was actually demonstrated. This directly impacts the validity of statements about outperforming established diagnostics in this case.\n\"The fast, adaptive, and *in situ* nature of antibiotic resistance profiling by nanopore sequencing would have therefore surpassed current clinical practice in accurately informing clinical management.\"\nThis sentence makes a comparative, practice-level conclusion (“surpassed current clinical practice”) that would normally require rigorous benchmarking or prospective clinical evaluation. In this manuscript, the primary evidence is detection of resistance gene calls from a single patient’s isolates, analyzed retrospectively, with no quantified error rates or uncertainty bounds. The phrase “would have therefore” asserts a counterfactual clinical benefit without demonstrating feasibility within the actual care timeline or showing that clinicians would have acted differently given the same information. Because the work is a single-case simulation, it cannot establish general superiority over standard-of-care across patient populations, sample types, or lab settings. Overstated counterfactual conclusions can mislead readers about the maturity of the proposed approach for clinical adoption. This is a significant concern under the Validity and Conclusions criteria.\n\"To date, the medical community is still awaiting large-scale clinical trials to establish the utility of NGS in different clinical settings; however, comprehensive funding and incentives for these studies are limited.\" ([1](#cite1))\nThis statement from the clinical NGS diagnostics literature highlights that translation from promising case reports to clinical utility typically depends on larger-scale clinical studies. The reviewed paper presents an instructive single case, but its strongest claims are phrased at the level of clinical practice improvement and superiority over established workflows. In light of this broader context, a single retrospective simulation cannot credibly support such practice-level conclusions. The external quote does not invalidate the paper’s feasibility demonstration, but it underscores why claims about clinical utility and practice change require more systematic evidence. The reviewed manuscript does not provide the kind of clinical-trial-style evaluation that would normally justify its most general statements. Therefore, the paper should substantially temper or re-scope those conclusions to match the evidence.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|GPT|2", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "This paper’s central “hidden resistance” result (Validity, Conclusions) relies on detecting a very small number of KPC-14-like reads in the pre-treatment isolate without presenting adequate controls or thresholds to rule out barcode switching/crosstalk or other false-positive mechanisms in multiplex nanopore sequencing.\n\n\"Our real-time genomics approach importantly also detected one copy of the KPC-14 resistance gene in the pre-treatment isolate; while this one copy would have been too little evidence to predict phenotypic CAZ-AVI resistance, our simulation of the adaptive application of real-time genomics in the clinic showed us that less than 20 hours of additional sequencing would have resulted in the detection of four more highly accurate copies of KPC-14 (Table 1). The second KPC-14 gene copy would have already been detected after two hours of additional sequencing and could have rapidly influenced antibiotic treatment through the early detection of CAZ-AVI resistance potential (Supplementary Figure 2; Methods).\"\nThe paper’s clinical argument hinges on the interpretation of 1–5 detected “copies” of a resistance gene as actionable early evidence of hidden resistance potential. However, the manuscript does not define a validated minimum-read threshold for a positive call in this setting, nor does it present negative controls (e.g., barcode-only controls, blank extractions) that would contextualize single-read detections. Because the key pre-treatment claim starts from exactly one detected copy, even low-rate cross-sample read misassignment could change the conclusion materially. The language “could have rapidly influenced antibiotic treatment” is therefore not supported without a quantified false-positive risk at the stated evidence levels. In clinical genomics, especially when minority variants are claimed, orthogonal validation (e.g., targeted PCR/qPCR, repeat library preps, independent sequencing) is common to confirm low-frequency signals. The absence of such validation makes the main “hidden resistance” conclusion fragile.\n\"Nanopore libraries were generated using the SQK-RBK004 Rapid Barcoding Kit and sequenced on an Oxford Nanopore Technologies MinION MK1b device... attaching one barcode per sample.\"\nThis sentence confirms that the two isolates were multiplexed using rapid barcoding, which introduces a well-known need to assess barcode misassignment and switching when interpreting rare reads. The manuscript does not report any demultiplexing quality-control metrics, barcode-balance statistics, or an estimate of barcode crosstalk for this run. Without those controls, it is difficult to exclude the possibility that a small number of reads assigned to the pre-treatment barcode originated from the post-treatment isolate (which has many KPC-14-like reads). This concern is amplified because the key pre-treatment evidence begins at a single detected read, which is within the range that could plausibly arise from low-level misassignment. Standard practice for multiplexed sequencing-based diagnostics typically documents cross-contamination controls when low-frequency calls are central to the claim. The paper’s methodology section does not provide that level of assurance.\n\"Additionally, we chose to only include respective KPC-2 and KPC-14 resistance genes with detection accuracies above 90% to minimise the chances of false positive resistance gene detection.\"\nThe paper’s primary safeguard against false positives is a per-hit “accuracy” threshold, but this does not address other major sources of false positives for rare-read claims, such as barcode switching, sample carryover, or contamination. Moreover, the manuscript does not explain how this “accuracy” is computed by the EPI2ME protein-homolog model, so readers cannot translate it into an expected false-positive probability for single-read detections. Filtering on an internal alignment/score metric is not equivalent to validating that the read truly originates from the sample’s DNA rather than misassignment. Because the conclusion depends on a very small number of reads, a robust analysis would typically combine score thresholds with explicit minimum read counts and run-specific cross-talk estimates. The paper provides neither a principled threshold for calling low-abundance KPC-14-like reads nor an uncertainty analysis of these calls. This undermines the validity of the “hidden resistance” finding.\n\"However, false positives may be introduced because of sequencing errors present in individual reads or DNA contamination from other organisms. Setting minimum thresholds for the number of reads needed for a positive result can help overcome read error problems.\" ([2](#cite2))\nThis external guidance directly addresses the reviewed paper’s situation: calling resistance determinants from raw reads is vulnerable to read-level errors and contamination, and minimum-read thresholds are a standard mitigation. The reviewed manuscript emphasizes detection of one read and then a handful more reads as clinically meaningful, but it does not specify or justify a minimum threshold for declaring presence of a low-abundance gene. The quote highlights that single-read detections are a known risk zone for false positives, and that principled thresholds are part of common practice when interpreting raw-read resistance calls. In the reviewed work, the absence of an explicit threshold and its validation is particularly problematic because the “hidden resistance” conclusion depends on minority evidence. Therefore, the external source supports the criticism that the paper’s control strategy is insufficient at the evidence levels used. This is a major issue for validity and conclusions.\n\"We also found cross-sample chimeric reads (0.3%) and evidence of barcode switching (0.3%) in our dataset, which likely arise during library preparation and may be detrimental for quantitative studies that use multiplexing.\" ([3](#cite3))\nThis published evaluation of nanopore barcoding demonstrates that barcode switching and cross-sample artifacts can occur at non-negligible rates in multiplex ONT workflows. The reviewed paper’s key claim depends on interpreting 1–5 reads as evidence of a low-abundance resistance gene in one barcode bin, i.e., a quantitative minority signal. Even a fraction of a percent of barcode switching can plausibly generate a small number of misassigned reads when the other sample contains dozens of true reads for the same gene (as reported for the post-treatment isolate). The reviewed manuscript does not measure or bound barcode switching for its own run, which is essential given its reliance on rare-read evidence. The quote underscores that this is not a hypothetical concern but an observed phenomenon in ONT multiplexing. As a result, without explicit controls, the manuscript cannot robustly support its low-abundance inference. This directly affects the validity of the “hidden resistance” narrative.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|GPT|3", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "This paper draws a strong mechanistic conclusion (Conclusions, Validity) that the resistance shift was caused by selection of a low-abundance KPC-14-like plasmid variant within a complex infection, but the presented genomic evidence does not rule out plausible alternatives such as within-host evolution of KPC variants or other resistance mechanisms.\n\n\"These results suggest that the observed change in antibiotic resistance might have been caused by a complex infection of the same *K. pneumoniae* lineage with a low-abundance KPC-14-carrying IncN plasmid which became dominant due to its evolutionary selective advantage under CAZ-AVI exposure.\"\nThis sentence proposes a specific causal mechanism—pre-existing low-abundance plasmid variation becoming dominant under selection—as the explanation for the phenotype change. However, the manuscript presents this as a suggestion without a formal competing-hypotheses analysis or quantitative within-sample plasmid frequency estimation across timepoints beyond a small number of detected resistance-gene reads. The fact that the isolates share ST147 and have similar IncN plasmids does not, by itself, establish that a minority plasmid population existed pre-treatment rather than arising via mutation, recombination, or acquisition during therapy. The evidence shown does not include a within-host evolutionary analysis (e.g., SNP distances, structural variation comparisons, or temporal dynamics) that would strengthen the selection-from-standing-variation claim. In clinical pathogen genomics, distinguishing mixed infection from within-host evolution typically requires deeper sampling and explicit genomic comparisons across isolates and/or timepoints. Because the mechanistic narrative is central to the paper’s significance, leaving alternatives unaddressed weakens the robustness of the conclusion. This is consequential for how broadly the findings can be interpreted.\n\"We found that the pre- and post-treatment isolates consisted of the same emerging high-risk sequence type ST147\\(^{15}\\).\"\nReporting that both isolates are ST147 supports relatedness at a coarse typing level, but ST assignment does not resolve whether the post-treatment resistance determinant emerged de novo within-host or was present as a minor subpopulation. Many distinct strains can share the same ST, and even within a single lineage, clinically important resistance changes can occur via mutation, gene amplification, or plasmid remodeling during treatment. The manuscript does not present finer-grained genomic distance measures (e.g., cgMLST allele differences or SNP counts between isolates) in the main text to support a mixed-plasmid infection model over within-host evolution. Without such evidence, the ST result is insufficient to justify the specific causal story advanced in the paper. The mechanistic claim is therefore more speculative than the manuscript’s language suggests. This matters because the proposed advantage of real-time genomics is precisely to detect such complex dynamics reliably.\n\"Upon submission of the post-treatment bacterial isolate to the German National Reference Center for Gram-Negative Bacteria (...), the KPC resistance gene that our workflow defined as KPC-14 was identified as a previously unseen KPC and named KPC-159...\"\nThis statement shows that the workflow’s key resistance-gene call (KPC-14) was revised to a previously unseen variant (KPC-159) by a reference center. While KPC-159 is reported as highly similar to KPC-14, the fact that a novel variant was involved increases the importance of carefully characterizing evolutionary trajectories and the timing of variant emergence. The manuscript does not present functional assays directly attributing the resistance phenotype to KPC-159, nor does it show detailed comparative genomics that could separate pre-existing minority presence from emergence during therapy. This is especially relevant because single amino-acid changes in KPC enzymes are known to shift CAZ-AVI resistance and carbapenem susceptibility profiles. Therefore, the mechanistic conclusion that a low-abundance plasmid became dominant is not uniquely supported by the evidence presented. The reference-center re-annotation reinforces that the precise variant dynamics require stronger substantiation.\n\"This study investigates the novel KPC-190 variant, identified in a hypervirulent ST11-K64 *K. pneumoniae* strain during CZA therapy, which confers resistance to CZA while partially restoring carbapenem susceptibility.\" ([5](#cite5))\nThis external case demonstrates that KPC-variant emergence during ceftazidime-avibactam therapy can produce the same qualitative phenotype pattern emphasized in the reviewed manuscript (CZA resistance with reduced carbapenem MICs). The existence of such within-host evolutionary trajectories makes it essential for the reviewed paper to more rigorously distinguish between selection of pre-existing low-abundance plasmids and de novo variant emergence under treatment pressure. The reviewed paper does not provide the level of genomic or experimental evidence (e.g., variant reconstruction, transformation assays, enzyme kinetics) that would be expected to confirm a specific mechanism. The external quote does not refute the reviewed hypothesis, but it shows that alternative explanations are plausible and documented in the literature. Therefore, the reviewed manuscript’s mechanistic narrative should be framed more cautiously or supported with additional analyses. Without that, the conclusion is not robust.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|GPT|4", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "This paper does not provide sufficiently accessible data identifiers and executable computational materials (Data and methodology) to reproduce the central resistance-gene timing and plasmid inferences, and it relies on external web services without providing complete run artifacts needed for independent verification.\n\n\"All FAST5 nanopore sequencing data has been uploaded to NCBI (https://www.ncbi.nlm.nih.gov, SRA submission: SUB13974279).\"\nThe manuscript provides only an SRA submission identifier, which is not the standard public accession format used for discovery and reuse (e.g., PRJNA/SRR). As written, an independent reader cannot reliably locate or download the data needed to rerun the analyses and verify the claimed KPC copy-number timeline. Because the paper’s most important claims depend on rare-read detections and timing, access to the raw reads is essential for reproducibility. Providing a non-actionable identifier effectively blocks independent confirmation of the key results. This is a major issue because case-based claims can be sensitive to pipeline settings and demultiplexing behavior that must be verified on the original data. The reproducibility gap therefore affects the credibility of the conclusions.\n\"A submission has a temporary non-public ID in the form of **SUB#**.\" ([6](#cite6))\nThis NCBI documentation clarifies that SUB identifiers are temporary and non-public, which explains why they are not sufficient for community access or verification. In the reviewed paper, the only data locator provided is a SUB number, so the dataset may not be findable or publicly retrievable at the time of reading. For reproducible computational biology, readers need stable public accessions (e.g., BioProject/Run accessions) that are searchable and resolvable. This matters more here because the study’s main finding depends on low-frequency reads, for which independent reanalysis is particularly important. The documentation therefore directly supports the claim that the current data-availability statement is inadequate for reproduction. The paper should provide public accessions or an alternative verifiable data release.\n\"After you have successfully completed your submission, the SRA will send an email notification together with the BioProject accession (in the form of **PRJNA#**) that you can use to reference your data in your publication(s).\" ([6](#cite6))\nThis documentation indicates that publications should reference the BioProject accession rather than a temporary SUB identifier. The reviewed manuscript does not provide a PRJNA (or SRR/SAMN) accession, so it does not follow the standard practice recommended by the archive itself for referencing data in publications. That omission impairs both discoverability and verification, since many tools and workflows expect PRJNA/SRR identifiers. In a study centered on a particular dataset and its temporal resistance-gene detections, correct archival referencing is not a minor administrative detail; it is necessary for scientific scrutiny. The quote makes the gap concrete: the paper is not providing the stable identifier that would enable reproducibility. This is a significant methodology shortcoming.\n\"Additionally, we uploaded the sequencing reads to BugSeq (https://bugseq.com/academic) for automated functional annotation of the plasmid genomes including resistance gene detection...\"\nThis step places part of the analysis in an external web service, which can hinder reproducibility if the exact database versions, parameters, and outputs are not archived and shared. The manuscript does not provide the BugSeq job identifiers, result files, or a complete description sufficient to rerun the same analysis independently. For reproducible genomics, reliance on third-party platforms is acceptable only when accompanied by exported artifacts and precise versioning, since web services can change over time. This is especially important when the results are used to support mechanistic claims about plasmid carriage and gene localization. Without the service outputs, reviewers cannot verify whether the same plasmid annotations and resistance calls would be obtained. Thus, the methodology description is not sufficient for independent reproduction of key intermediate results.\n\"All computational scripts for processing the FAST5 data are available here: https://github.com/Genomics4OneHealth/Klebsiella_pneumoniae_KPC_nanopore_sequencing\"\nWhile a repository link is helpful, the local code provided with this submission consists of generic placeholder commands rather than a complete, runnable pipeline tied to the reported dataset and parameters. The manuscript also relies on proprietary EPI2ME workflows with specific version strings, which are not provided as executable scripts that can be run offline and audited. For a paper whose key quantitative conclusion is a gene-detection timeline (e.g., “second copy after two hours”), reproducibility requires exact commands, demultiplexing settings, and the mapping from read timestamps to gene hits. The manuscript does not provide these run artifacts in a way that allows independent reconstruction. Therefore, the code-availability statement does not currently translate into a reproducible analysis. This is a major issue under the Data and methodology criterion.\n```bash\nguppy_basecaller -i /input/directory -s /output/directory --config configuration.cfg\n```\nThis code block (from the provided notebook) is an illustrative template rather than an executable, study-specific command: it contains placeholder paths and omits key options needed to reproduce the manuscript’s exact basecalling setup. Similar placeholder-style commands appear throughout the provided materials, and they do not encode the dataset’s file structure, barcoding/demultiplexing procedure, or the parameterization used for the reported results. In reproducible clinical genomics, the analysis should be runnable from raw data with pinned software versions and complete commands (or a workflow engine) that produces the reported tables and figures. Here, the provided code does not enable that outcome, especially given the reliance on EPI2ME and other external services. Because the central claim depends on low-count detections and timing, any ambiguity in preprocessing can change the result. This evidence supports that the shared code is not sufficient for independent verification.\n\"All aspects of the NGS diagnostic pipeline remain variable, including clinical specimen collection, sequencing parameters, data analysis/interpretation, and data reporting. Such details must be established before clinical outcomes can be systematically examined.\" ([1](#cite1))\nThis external statement underscores why detailed, stable reporting of data and computational steps is essential in clinical sequencing contexts. The reviewed manuscript’s core claims depend on specific pipeline behaviors (demultiplexing, read filtering, resistance gene matching, time-resolved counting), but the provided materials do not fully specify or export the necessary artifacts to reproduce them. In particular, using a non-public SUB identifier and relying on external platforms without archived outputs prevents independent validation of the results. The quote highlights that variability in sequencing parameters and analysis pipelines is a known barrier; thus, incomplete reporting is a significant methodological flaw rather than a minor documentation issue. The reviewed manuscript does not meet the level of transparency needed for readers to assess robustness and error modes. Consequently, the reproducibility of the key findings is not adequately supported.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "The paper's central claim of detecting \"hidden\" antibiotic resistance (KPC-14) in the pre-treatment isolate relies on a single Nanopore read (or extremely few reads), which is statistically insufficient to distinguish a true variant from a sequencing error without orthogonal validation.\n\n\"Our real-time genomics approach importantly also detected one copy of the KPC-14 resistance gene in the pre-treatment isolate\"\nThe authors base their discovery of \"hidden\" resistance on a single \"copy\" (read) of the KPC-14 gene. Given that KPC-14 is defined by a specific 6-bp deletion (Gly242-Thr243) compared to the dominant KPC-2, and Nanopore R9.4.1 sequencing has a known high error rate for indels [1], a single read with this deletion is indistinguishable from a sequencing artifact. Relying on N=1 for such a critical clinical finding is statistically unsound.\n\"The second KPC-14 gene copy would have already been detected after two hours of additional sequencing\"\nThis statement confirms that the \"detection\" is based on the accumulation of individual reads over time. Finding only two reads after ~17 hours of sequencing (15h initial + 2h additional) further highlights the extreme paucity of evidence. Without error correction or validation, these few reads could easily be false positives, which would lead to incorrect clinical decisions (e.g., withholding a potentially effective drug).\n\"In the pre-treatment isolate, we detected the presence of accurate (> 90%) KPC-2 gene copies (n=40; Table 1)\"\nThe authors report 40 reads for KPC-2 and 1 read for KPC-14. A 1:40 ratio (2.5%) is within the range of sequencing noise for specific indel errors in Nanopore data, especially if the deletion occurs in a homopolymer or difficult-to-sequence region. The paper lacks an error profile analysis to demonstrate that this specific deletion is not a common systematic error.\n\nReferences:\n[1] [Comparison of R9.4.1/Kit10 and R10/Kit12 Oxford Nanopore flowcells and chemistries in bacterial genome reconstruction](https://www.biorxiv.org/content/10.1101/2022.04.29.490057v2.full-text)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "The use of the term \"Copy Number\" (CN) in Table 1 and the text is undefined and appears to represent raw read counts, which is misleading and obscures the low statistical confidence of the findings.\n\n\"Table 1... CN\" with values \"40\", \"1\", \"147\", \"4\"\nIn genomics, \"Copy Number\" (CN) typically refers to the genomic copy number (i.e., the number of copies of a gene per genome or plasmid). However, the values in Table 1 (e.g., 1, 4, 40, 147) and the context of \"detected... copies\" strongly suggest these are raw read counts. Using \"CN\" to denote read counts is non-standard and potentially misleading, as it implies a calculated genomic feature rather than raw data.\n\"detected one copy of the KPC-14 resistance gene\"\nIf \"copy\" means \"read\", then the authors are claiming detection based on a single data point. If \"copy\" means \"genomic copy\", it is unclear how they calculated a CN of 1 from what is likely a single read or very low coverage. This ambiguity makes it difficult to assess the robustness of the data.\n\"less than 20 hours of additional sequencing would have resulted in the detection of four more highly accurate copies\"\nThis phrasing further conflates \"reads\" with \"copies\". In a clinical context, \"four copies\" sounds like a confirmed biological presence (e.g., 4 plasmids), whereas \"four reads\" is a very different and much weaker level of evidence. The authors should explicitly state \"read count\" to be transparent about the data quantity.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "The claim that \"real-time genomics\" can effectively detect hidden resistance is overstated, as the detection of the low-abundance variant required extensive simulated sequencing (>15 hours) and retrospective analysis, which contradicts the \"rapid\" narrative presented in the abstract and figures.\n\n\"real-time genomic workflow delivers first data after ~1.5 hours\" (Figure 1 caption)\nThis caption suggests a rapid turnaround time. However, this likely refers only to the start of sequencing or species ID. For the central claim of the paper—detecting the \"hidden\" KPC-14—the authors admit it required much longer.\n\"sequenced the pre-treatment isolate for another 20 hours... The second KPC-14 gene copy would have already been detected after two hours of additional sequencing\"\nThis implies that to find just *two* reads of the hidden resistance gene, a total of ~17 hours of sequencing (15h initial + 2h additional) was required. This timeline is far from the \"1.5 hours\" implied for the workflow and challenges the practical utility of \"real-time\" sequencing for detecting rare variants in a clinical setting.\n\"We processed the raw nanopore data using high-accuracy Guppy basecalling\"\nThe use of \"high-accuracy\" (HAC) basecalling is computationally intensive and typically performed offline or requires significant hardware acceleration. The \"simulation\" does not appear to account for the time required for HAC basecalling, assembly, and resistance prediction, which would further delay the \"real-time\" results beyond the sequencing time.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "The study lacks validation of the \"hidden\" KPC-14 variant using a gold-standard method (e.g., deep Illumina sequencing or specific PCR), which undermines the validity of the central finding given the high error rate of the primary method.\n\n\"In contrast to established diagnostics, real-time genomics can accurately identify complex antibiotic resistance patterns\"\nTo support the claim that Nanopore is superior to established diagnostics for this specific case, the authors must prove that the \"hidden\" resistance (KPC-14) was actually present in the pre-treatment isolate and not a sequencing error. The standard way to do this is with a higher-accuracy method like deep Illumina sequencing or a specific PCR assay targeting the deletion.\n\"detected one copy of the KPC-14 resistance gene in the pre-treatment isolate\"\nWithout orthogonal validation, the \"1 copy\" remains a putative finding. If it is a false positive, the entire premise of \"hidden resistance detection\" collapses. The authors compare their results to VITEK2 (phenotypic) but fail to compare to or validate with standard molecular methods that could confirm the genotype.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "This work is contributing to the overall improvement of the field and contributes as a well-needed case-study for genomic sequencing implementation into the routine clinical care, however, taking into account the increasing number of studies using Nanopore for AMR detection in real time, the current study lacks the novelty and direct impact, for which the expectation was set out by a well-written and catchy title (I was expecting to see something like metagenomic samples sequenced and resistance then detected in follow on samples in real-time, or multiple bacterial samples sequenced and overall impact has been shown).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "In the main text it is not straight away clear that you have been working with single colony purified samples after the samples have undergone routine microbiology procedures. And it is not clear that the authors have sequenced single or multi-colony samples?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "There are no mention of limitations of not doing a metagenomic sequencing on the patients samples to see if multiple types of Klebsiella pneumoniae or even other bacterial pathogens could have contributed to the change in AST results. Would such isolates be available?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "Was a blood sample available for the patient in the first days or only the Endo aspirate was taken?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "“Using this real-time genomic data, we correctly identified K. pneumoniae as the dominant pathogen in the pre- and post-treatment isolates.” This sentence makes it seem that you have not expected to see K. pneumoniae or were expecting multiple pathogens? This unfortunately adds to the confusion if only pure known-pathogen colonies were sequenced, or you have sequenced a streak of bacterial growth.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "Would authors please clarify for having different 15hr and 20hrs cut-offs for pre- and port-treatment isolates?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "Table 1. I have failed to find the explanation in the methods for how the accuracy was estimated in these cases? What did you use as your standards for comparison? It did not seem that the authors run biological and technical replicates of the same samples to confirm that the levels of detection were the same, especially in the situation where they were not necessary following a well-establish and tested methods for such scenarios (and its expected given that the field is rapidly evolving!). but having genomic data from biological and technical replicates – would have provided stronger evidence for if the KPC-2 and KPC-159/KPC-14 strains were co-existing already but were failed to be detected in time due to ratios of these mini-sub-populations present.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "More information and illustration of genes identified on the detected IncN plasmid would have been very informative – was this predicted to be mobilizable plasmid? Did it have all conjugation mechanism in place in both pre- and post- treatment samples? How did genetic contents of the plasmid carrying KPC-2 or KPC-14/KPC-159 compared? This would provide additional information that could explain the potential advantage of KPC-14/KPC-159 emergence in such short time or at least contribute to the better understanding on IncN plasmids.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Human_1|9", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "How many copies of plasmid replicons were found in comparison to copy numbers of the targeted genes? were there also any other resistance genes detected?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Human_1|10", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "“a new KPC resistance gene, KPC-159, that is very similar to the KPC-14 gene detected by our analysis (amino acid sequence similarity of 99.9%) and therefore conferred the same phenotypic antibiotic resistance” “- this sentence from the authors is very confusing, as now it raises questions was is KPC-14 reported here or the KPC-159? or all 3 were identified? if the latter, then what was the reasoning to report only KPC-14 in Table 1?", "reviewer_type": "human", "label": "error", "error_type": "Neglect", "label_origin": "expert+llm-filter"}
{"id": "prb|54|Human_1|11", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "A more detailed genetic description of the strains and the plasmids identified (and maybe even potential comparison to other Kp strains reported globally to carry the reported KPC-2, KPC-14) would contribute to the understanding how spread this strain could be?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "The use of Nanopore for rapid characterisation of bacteria and AMR predictions from blood stream infections (BSI) is not groundbreaking. Harris et al recently published work evaluating the performance of Nanopore for this purpose (Harris et al. Microbiology spectrum (2024). DOI: https://doi.org/10.1128/spectrum.03065-23). However, the novelty here lies in the real-time application of Nanopore. Yet, it remains uncertain if the authors achieved their intended objectives.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "The authors highlight lingering concerns about the precision of real-time genomics in predicting phenotypic antibiotic resistance, especially when juxtaposed with established diagnostic approaches - it would greatly benefit readers if these concerns were described alongside how this study addresses them. My concern is that the authors failed to identify the heterogeneity with regards to meropenem and CAZ-AVI resistance observed in this patient. This might be attributed to how isolates were chosen for sequencing (colony pick versus plate sweep), underscoring a limitation of isolate sequencing i.e. its inability to efficiently capture population heterogeneity among closely related bacteria within individual patients. Unfortunately, the authors haven't sufficiently addressed this limitation or proposed strategies for how they may be overcome.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "The authors describe the discovery of a \"new\" KPC resistance gene, which would be better described as a new allele. The novelty of this discovery is debatable, given its 99.9% amino acid sequence similarity to KPC-14 and its similar resistance phenotype.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "Initial sequencing took ~5 days, which raises questions about its comparative efficiency and cost-effectiveness against standard laboratory diagnostic procedures. Did the subsequent sequencing phase also take around five days? If so, did the cumulative time for characterising the infection's resistance profile approach ten days?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "While the entry cost for Nanopore sequencing is markedly lower than that of other sequencing platforms, the computational infrastructure required for high-quality base calling in a timely manner can sometimes surpass the sequencing platform's cost. It would be advantageous for the authors to delineate the computational infrastructure employed for bioinformatics analysis and whether it might pose a barrier to adopting and integrating whole-genome sequencing (WGS) into routine clinical practice.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "Lines 142-143 and Figure 1: In the comparison control vs LNB, 41 proteins are significantly expressed with a fold change larger than 2. Quote Figure A (Volcano plot) and not Figure B (Overlap).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "While the 10 proteins from the VM vs LNB comparison are visible on Figure 1B, 43 proteins (33+7+3) are recorded on Figure 1B for control vs LNB. What makes the difference between 41 and 43?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "Line 145: This sentence refers to Figure 1B, not Figure 1C", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "Line 202: The number of proteins identified in the plasma samples (median of 268 proteins) is quite low, which is not surprising in the absence of depletion or prefractionation, but only allows the more abundant proteins to be detected. The authors chose to use a very short 8 cm column (probably to increase the number of samples per day). What impact did this length of column have on the number of proteins identified, compared with previous plasma studies in the literature using much longer columns?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "Figure 3A: To be consistent note “Control vs LNB” on the Volcano plot and not “LNB control vs LNB”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "Figure 3B: Line 205 states that 61 proteins are significantly different in VM vs LNB. However, on Figure 3B, a total of 68 proteins (28+33+4+3) are in the corresponding circles. Same remark for the 63 proteins stated Line 206 (LNB vs control), while a total of 69 proteins (33+30+3+3) are in the corresponding circles. What make these differences?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Human_3|7", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "Line 194 (Fig 3B legend): As seen on Figure 3A and Supplemental Table 2, only 2 proteins (VWF, S100A9) exhibit a fold change larger than 2 in LNB vs control. Similar remark for VM vs LNB with only 6 proteins with a fold change larger than 2. There must be an error in the, since all the significantly proteins are represented, and not only the significant proteins with a fold change larger than 2.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Human_3|8", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "Line 207: This sentence refers to Figure 3B, not Figure 3C", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Human_3|9", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "Given that, for plasma, all the significant proteins have been taken into account (and not just those that vary with a fold change larger than 2 as in CSF), are there any consequences for the robustness of a blood-based clinical test?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|54|Human_3|10", "source": "prb", "split": "test", "paper_id": "prb54", "comment": "Line 636 (Mat & Meth): As the MS equipment and the column are different from those used in the cited publications44,45,46, the authors should give more details on LC conditions (e.g. gradient duration) and MS acquisition parameters (or cite additional publications).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Claude|3", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "The plasma classifier demonstrates a 16-percentage-point drop in AUC (from 0.96 to 0.80) and a 35-point drop in MCC (from 0.83 to 0.48) between development and validation cohorts, suggesting overfitting that is inadequately addressed in the manuscript.\n\n\"Of the twelve models tested, the SVC model obtained the best performance in the test set (Supplementary Figure 9) with an AUC of 0.96 (std.=0.03) and a MCC of 0.83 (std.=0.008) (Figure 4A). When applied on the validation cohort the model obtained an AUC of 0.80 (std.=0.02) and a MCC of 0.48 (std.=0.04)\"\nThe difference between development performance (AUC=0.96) and validation performance (AUC=0.80) represents a substantial 16-percentage-point drop. More concerning is the MCC drop from 0.83 to 0.48, which is below the 0.5 threshold often considered necessary for a useful classifier. An MCC of 0.48 indicates the classifier performs only marginally better than random chance. This dramatic performance degradation is a hallmark of overfitting, where a model learns noise and spurious correlations in the development data that do not generalize to new samples. The combination of data leakage from feature selection (Item 1) and a small plasma development sample (n=27 LNB, n=48 controls) creates conditions highly favorable for overfitting.\n\"In plasma, LNB was distinguished from controls with an AUC of 0.80.\"\nThe abstract reports the validation AUC of 0.80 without mentioning the development AUC of 0.96 or discussing the substantial performance gap. This selective reporting obscures the evidence of overfitting and may mislead readers about the robustness of the plasma classifier. A more transparent presentation would acknowledge the performance drop and discuss its implications for clinical utility. The title claims proteomics enables \"rapid and accurate\" diagnosis, but an AUC of 0.80 with MCC of 0.48 in validation represents only moderate discriminative ability.\n\"Applying the feature selection incorrectly prior to the cross-validation showed a bias of up to 0.15 in AUC-ROC\" — [Demircioğlu (2021)][1]\nThe observed 0.16 AUC drop in plasma is consistent with the bias magnitude reported for incorrect feature selection methodology. This suggests that much of the apparent performance in the development cohort may be attributable to data leakage rather than genuine predictive signal. When the model is applied to the independent validation cohort, where this artificial boost is absent, performance drops substantially. This pattern further supports the conclusion that the methodology introduces optimistic bias in development set performance.\n\nReferences:\n[1] [Demircioğlu A. \"Measuring the bias of incorrect application of feature selection when using cross-validation in radiomics.\" Insights into Imaging. 2021;12(1):172.](https://pmc.ncbi.nlm.nih.gov/articles/PMC8613324/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Claude|4", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "The plasma validation cohort contains only 10 LNB patients, which is insufficient to reliably estimate diagnostic performance metrics and leads to high uncertainty in the reported AUC values.\n\n* Quote (Table 1): \"Plasma Validation - Lyme neuroborreliosis: n=10\"\nWith only 10 LNB patients in the plasma validation cohort, the statistical power to reliably estimate diagnostic performance is severely limited. For a binary classifier, having only 10 positive cases means that each misclassified patient changes the sensitivity estimate by 10 percentage points. This small sample size leads to wide confidence intervals around the AUC estimate, making it difficult to assess the true diagnostic utility of the plasma classifier. The paper reports AUC of 0.80 (std.=0.02) but this standard deviation reflects only cross-validation variability, not the sampling uncertainty from the small validation cohort.\n\"It was not deemed feasible to develop a model for the discrimination of viral meningitis and LNB due to the low number of viral meningitis cases\"\nThe authors appropriately recognize that small sample sizes preclude certain analyses (VM vs. LNB discrimination in plasma). However, they do not apply similar scrutiny to the LNB vs. control classification, where the LNB validation sample (n=10) is even smaller than the viral meningitis validation sample (n=18). If 18-20 VM cases were deemed insufficient for model development, the use of 10 LNB cases for validation raises similar concerns about statistical reliability. The claim of \"accurate diagnosis\" in the title is not well-supported when validation is based on only 10 positive cases.\n\"The Plasma Development cohort included a total of 95 plasma samples from patients with LNB (n=27), viral meningitis (n=20) and controls (n=48) whereas the plasma validation cohort consisted of 80 plasma samples\"\nThe imbalance between development (n=27 LNB) and validation (n=10 LNB) cohorts is notable. The validation cohort has only 37% as many LNB patients as the development cohort, making it underpowered to reliably evaluate model generalizability. Standard guidelines for diagnostic accuracy studies recommend larger validation cohorts to ensure precise estimation of sensitivity and specificity. The combination of small sample size with potential overfitting (Item 3) means the reported plasma performance metrics should be interpreted with considerable caution.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|GPT|1", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "The manuscript’s reported development/validation performance is not a valid estimate of generalization because key preprocessing steps (missingness filtering thresholds, variational-autoencoder imputation, and ComBat batch correction) are fit on pooled data before splitting into development vs validation cohorts, which breaks the intended independence of the validation cohorts.\n\n“Samples from the two sites of origin were kept separate in the subsequent analyses to preserve independent cohorts for model development and validation.”\nThis sentence establishes that the paper’s central evidentiary claim relies on a clean separation between development and validation cohorts. If any data-driven preprocessing is fit on the combined set, then information from the validation cohort influences the representation used to train the model, violating this independence. This is especially consequential for proteomics where missingness patterns and batch effects can differ across collection periods and sites. Because the reported AUC/MCC values are used to argue clinical diagnostic potential, any leakage invalidates the strength of that conclusion. The statement therefore creates a clear standard that the provided pipeline must meet for the validation to be credible. The code below shows that the standard is not met.\n“Initially, a stringent filter for missing data was applied: 1) samples with low protein count, defined by a value below 1.5IQR from the 25th quantile of the combined distribution, were excluded, and 2) proteins with a missingness of more than 40% across samples were excluded… The remaining missing values were imputed with a variational autoencoder using the PIMMS software… Batch correction was executed using combat…”\nThis description indicates that filtering thresholds depend on a “combined distribution” and that imputation and batch correction are learned from the data. When “combined” spans development and validation cohorts, the resulting feature space is partially optimized using the validation cohort’s distribution, which can make the downstream classifier look better than it would on truly unseen data. Even though ComBat and VAE imputation are “unsupervised,” they still estimate parameters from the full sample set and therefore leak validation-cohort information into training-time transformations. This is a well-known source of optimistic bias in model evaluation because the test/validation set no longer reflects a real deployment scenario. The manuscript does not describe safeguards (e.g., fitting imputation/ComBat only on development and applying frozen transforms to validation). As a result, the reported validation performance cannot be interpreted as an independent confirmation.\n```python\n# 3) impute\ndf_wide = pg_wide[filter_info.columns]\nimputed_data_csf = pimms_imputation(df_wide)\n\n# 4) correct for plate effect\nimputed_data_csf = pd.merge(pg_long_csf[['sample_id','batch','type','study_cohort']].drop_duplicates(), imputed_data_csf, left_on = 'sample_id',right_index = True, how = 'right')\nimputed_data_csf.batch.fillna('No_plateinfo', inplace = True)\nindex_cols = ['sample_id', 'batch', 'type', 'study_cohort']\ncorrected_data_csf = batch_correction(imputed_data_csf.set_index(index_cols), plate_lst = imputed_data_csf.batch.tolist())\n```\nThis code (from the provided `data_prep.ipynb`) fits the VAE imputation (`pimms_imputation`) and then runs ComBat batch correction to produce `corrected_data_csf` without first restricting to the development cohort. Because `pg_long_csf` contains samples with a `study_cohort` field (development vs validation), the imputer and ComBat parameters are learned using both cohorts unless explicitly subset beforehand. This directly contradicts the intended “independent cohorts” separation described in the paper. The resulting corrected matrix embeds information from validation samples (e.g., their missingness structure and batch distributions) into the transformation applied to the development samples. Any subsequent model training and evaluation on the validation cohort is therefore contaminated. This is a major validity threat rather than a minor implementation detail.\n```python\ncohorts = [['csf_development','csf_validation'],['csf_development'],['csf_validation']]\nnames = ['csf_combined','csf_development','csf_validation']\nfor i in range(len(cohorts)):\n    cohort = cohorts[i]\n    aps_data = 2**corrected_data_csf.loc[(corrected_data_csf.index.get_level_values('type')=='sample')].droplevel(['type', 'batch','study_cohort']).T\n    aps_data.columns = ['csf'+x for x in aps_data.columns.tolist()]\n    aps_data = aps_data[aps_meta[aps_meta.study_cohort.isin(cohort)].sample_id.unique().tolist()]\n    aps_data.to_csv('../submission/aps_data_corrected_{}.tsv'.format(names[i]), sep = '\\t', index = None)\n```\nThis code shows that development and validation TSVs are created by subsetting *after* `corrected_data_csf` has already been computed. That ordering is crucial: it means the “development” and “validation” exports share a common preprocessing model fit on pooled cohorts, so they are not independent datasets in the statistical sense. External validation is meant to test a fixed pipeline trained on development data only; here, the pipeline’s preprocessing has already absorbed information from validation. This can systematically inflate performance by removing cohort-specific artifacts that would otherwise challenge generalization. The same pattern appears for plasma (`corrected_data_blood`) in the same notebook, implying the plasma validation is also affected. Consequently, the main diagnostic-accuracy claims are not supported as stated.\n“Test data should never be used to make choices about the model. The general rule is to never call `fit` on the test data… it is important that these transformations are only learnt from the training data.” ([5](#ref5))\nThis guidance captures the core methodological principle violated by the pipeline: data-dependent transformations must be learned strictly on training/development data. Imputation and batch correction are exactly such learned transformations because they estimate model parameters from the observed matrix. Learning them on pooled development+validation data implicitly “fits on the test data,” even if no labels are used. This leads to overly optimistic performance estimates and reduces the credibility of any claimed validation. The manuscript’s framing of separate development/validation cohorts implies adherence to this rule, but the code demonstrates otherwise. Therefore, the evaluation is not aligned with common, well-established machine-learning practice for leakage-safe validation.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|GPT|2", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "The manuscript’s model-development procedure is likely to yield optimistically biased internal performance and unstable feature importance because it uses outcome-driven feature selection (univariable significance screening and RFECV) and hyperparameter search in a way that is not nested within the evaluation folds, contradicting best practices for high-dimensional omics classification.\n\n“Significant proteins identified by t-test analysis on the development cohorts were used as input features in the training data… For each algorithm, optimal hyperparameters and features were selected during cross-validation.”\nThis description implies that feature selection and hyperparameter optimization occur in a manner that is properly contained within the cross-validation procedure used to estimate performance. In high-dimensional proteomics, even small deviations from nested evaluation can dramatically inflate AUC because the same samples influence both feature selection and testing. The text does not explicitly state that t-test screening and feature-selection steps are repeated inside each fold, which is the key requirement to avoid selection bias. The phrase “selected during cross-validation” is therefore ambiguous and needs to be supported by a clearly nested implementation. The provided code indicates the opposite: several selection steps are fit once on a training matrix and then reused across evaluation splits. That mismatch undermines confidence that the reported “test set” (CV) performance is unbiased.\n```python\n# Differential expression analysis\ndiffs = []\ndfs = []\nfor groups in [['LNB','VM'],['LNB','control']]:\n    diff_df= dataset.diff_expression_analysis(groups[0],groups[1],column='diagnosis', fdr=0.05)\n    diff_df = diff_df[(diff_df.pval<0.05)]\n    diff_df = diff_df[(diff_df.log2fc.abs()>1)]\n    diff_df = diff_df['Protein.Group'].tolist()\n    diffs.append(diff_df)\n\n# save result\ncombined_lst = list(set(diffs[0]+diffs[1]))\n```\nThis code (from `csf_analysis.ipynb`) constructs the feature set `combined_lst` using differential expression over the development cohort. That is a supervised feature selection step because it uses the outcome labels (LNB vs VM/control) to choose features. If cross-validation performance is later computed using the same development samples without repeating this selection *inside each training fold*, then the evaluation is biased because the held-out fold influenced which features were available. This problem is especially acute in omics settings where many features are tested and a subset is selected for modeling. The manuscript reports “test set” AUCs with standard deviations, which readers will interpret as cross-validated estimates; such estimates become optimistic under this workflow. Without a nested selection procedure, the reported AUC/MCC on the “test set” cannot be trusted as an unbiased estimate.\n```python\nselector = RandomizedSearchCV(estimator=estimator, param_distributions=grid, cv=StratifiedKFold(no_cv), scoring = 'f1_weighted', n_jobs = -1)\nclf = selector.fit(X_train,y_train)\noptimal_model = clf.best_estimator_\n\nselector = RFECV(optimal_model, cv=5, scoring='f1_weighted')\nselector = selector.fit(X_train, y_train)\nX_reduced = X_train[:,selector.support_]\n\ncv = StratifiedKFold(n_splits=no_cv)\nfor i, (train, test) in enumerate(cv.split(X_reduced, y_train)):\n    classifier.fit(X_reduced[train], y_train[train])\n    y_prob = classifier.predict_proba(X_reduced[test])[:,1]\n    aucs.append(round(roc_auc_score(result.observed,result.probability),2))\n```\nThis sequence shows that hyperparameter search (`RandomizedSearchCV`) and RFECV feature elimination are fit on all of `X_train` before computing the reported cross-validated AUCs. The subsequent CV loop then evaluates performance on folds that were already used (indirectly) to pick both hyperparameters and the RFECV feature mask, which violates the core idea of nested cross-validation. In a correct nested design, the selection of hyperparameters and features must be re-done inside each outer fold using only that fold’s training split, so that the outer test fold remains untouched by any selection decisions. As written, the “test” fold performance is expected to be optimistically biased because the model configuration is tuned with information from the entire `X_train`. This can inflate both AUC and the apparent stability of selected proteins and SHAP importances. Therefore, the internal “test set” performance reported in Figure 2/4 is not a robust basis for model comparison or for claiming diagnostic accuracy.\n“To correct for this selection bias, it is essential that cross-validation or the bootstrap be used external to the gene-selection process.” ([4](#ref4))\nThis sentence directly addresses the situation in which features are selected using all samples and then performance is estimated with cross-validation that does not encapsulate that selection. The paper under review uses proteomics as high-dimensional input and explicitly selects “significant proteins” prior to modeling, which is the same methodological pattern discussed in this classic selection-bias warning. The cited guidance is not limited to microarrays; the logic applies to any high-dimensional biomarker setting including proteomics panels. If the manuscript’s CV does not re-run feature selection within each fold, then the measured error/AUC is biased downward (performance biased upward). This bias can be substantial and may change which algorithm appears “best,” undermining the conclusions about LR vs SVC superiority. The code excerpts above indicate that the CV is not “external to the selection process,” matching the failure mode described here.\n“Dev Val 4.5 Was selection of predictors based on univariable analysis avoided?” ([3](#ref3))\nThis PROBAST signaling question highlights that univariable screening for predictors is a recognized source of bias in prediction-model analyses. The manuscript describes and implements univariable t-test–based screening (“significant proteins”) as a gateway to the multivariable model, which maps directly onto the concern captured by this question. Even when followed by multivariable modeling, univariable preselection can yield unstable predictor sets and overly optimistic performance, particularly when combined with flexible model selection. The paper does not provide evidence that this risk was mitigated by a fully nested evaluation design or by prespecified predictors. Because the main claim is that a protein “panel” can diagnose LNB, bias in predictor selection threatens both the validity of the panel and its reproducibility. Under PROBAST’s framework, this would raise risk-of-bias concerns in the “Analysis” domain.\n\nReferences:\n[1] [Collins GS, Reitsma JB, Altman DG, Moons KGM. Transparent reporting of a multivariable prediction model for individual prognosis or diagnosis (TRIPOD): the TRIPOD statement. *BMJ* 2015;350:g7594.](http://med-fom-obgyn.sites.olt.ubc.ca/files/2015/02/Mar-1315-TRIPOD-statement-2015.pdf)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|GPT|3", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "The manuscript’s conclusion that plasma proteomics enables “accurate” LNB diagnosis is not statistically well supported because the plasma validation cohort contains only 10 LNB cases and the paper reports AUC/MCC with “std.” rather than appropriate precision measures (e.g., confidence intervals), making the reliability of the plasma AUC=0.80 claim unclear.\n\n“the plasma validation cohort consisted of 80 plasma samples from patients with LNB (n=10), viral meningitis (n=18), controls (n=20)…”\nA validation set with only 10 positive cases is typically insufficient to provide a stable estimate of discrimination (AUC) for a clinical diagnostic classifier, especially when the model was tuned on a separate development cohort. With so few positives, single misclassifications can materially change estimated performance, and estimates can vary widely across resampling methods. This limitation is not merely about “power”; it affects the credibility of the reported point estimate (AUC=0.80) and makes comparisons to other approaches unreliable. The small n also makes subgroup analyses (e.g., across other Lyme manifestations) particularly fragile. Because the paper’s abstract and discussion elevate plasma as a less invasive diagnostic opportunity, the evidence base for that claim must be quantitatively tight. The study design as reported does not provide that tightness.\n“When applied on the validation cohort the model obtained an AUC of 0.80 (std.=0.02) and a MCC of 0.48 (std.=0.04) (Figure 4A).”\nReporting “std.” for a single external validation cohort is difficult to interpret as statistical precision for the AUC itself. The validation cohort is fixed; the variability implied by “std.” appears to arise from repeated refits on different development splits rather than from sampling uncertainty in the validation estimate, which is not the standard way diagnostic-accuracy uncertainty is communicated. Without confidence intervals, readers cannot judge whether the true discrimination could plausibly be meaningfully lower (or higher) given the small number of positives. This matters because an AUC around 0.80 can be clinically useful in some contexts but insufficient in others, and the difference cannot be assessed without precision. Moreover, the manuscript uses these values to motivate clinical feasibility, so statistical uncertainty must be handled rigorously. As written, the reported plasma performance may be overstated in certainty.\n“Report performance measures (with CIs) for the prediction model” ([1](#ref1))\nTRIPOD explicitly identifies confidence intervals as an essential reporting element for prediction model performance. This requirement is especially salient here because the plasma validation cohort is small and therefore performance estimates are expected to be imprecise. AUC and MCC point estimates without CIs can mislead readers into overinterpreting small differences or overestimating robustness. TRIPOD’s guidance is widely used in clinical prediction and diagnostic modeling, making it a relevant benchmark for evaluating methodological reporting quality. The manuscript’s “std.” values do not substitute for CIs around externally validated performance estimates. Therefore, the statistical reporting does not meet common expectations for reliability assessment in clinical prediction.\n“Estimates of diagnostic accuracy and their precision (such as 95% confidence intervals)” ([2](#ref2))\nSTARD similarly emphasizes that diagnostic accuracy reporting should include precision measures such as 95% confidence intervals. This is not a stylistic preference; it is necessary for readers to assess statistical uncertainty and potential overfitting or instability. In the reviewed manuscript, AUC and MCC are central claims but are not accompanied by CIs, even where sample sizes strongly motivate them. The plasma validation result (n=10 positives) is precisely the scenario where CIs can be wide and potentially alter interpretation of “accurate diagnosis.” By omitting CIs, the paper makes it impossible to gauge whether the observed performance would likely replicate in a new cohort. This weakens the evidentiary basis for the plasma-focused conclusions.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|GPT|4", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "The manuscript’s framing that proteomics could reduce diagnostic delay and reliance on lumbar puncture is not supported by the evaluated population and discovered signatures, because LNB cases are defined by intrathecal antibody positivity and the dominant CSF signature consists of immunoglobulins, which risks reproducing the same temporal limitations of antibody-based diagnostics.\n\n“Early diagnosis remains challenging due to limited sensitivity of current methods and requires invasive lumbar punctures, underscoring the need for improved, less invasive diagnostic tools.”\nThis sentence positions the work as addressing two specific clinical gaps: early diagnostic sensitivity and reduced reliance on lumbar puncture via less invasive testing. Those goals require demonstrating that the proposed proteomics+ML signature detects LNB earlier than (or at least independently from) the established intrathecal antibody response, and that plasma testing can reliably substitute for CSF testing. However, the subsequent study design and case definition determine what stage of disease is actually represented in the “true positive” group. If positives are primarily later-stage immune responders, then performance estimates may not translate to earlier, antibody-negative presentations that drive diagnostic delay. Thus, the framing creates a strong expectation that the evaluation cohort includes clinically difficult early cases. The evidence below suggests the study does not establish this.\n“LNB: Patients diagnosed with LNB based on a first-time positive *B. burgdorferi*-specific intrathecal antibody test…”\nThis case definition ties “ground truth” LNB status directly to an antibody-based CSF measure, which is itself known (per the paper’s introduction) to be insensitive early. Therefore, the classifier is not evaluated on antibody-negative LNB cases, and cannot demonstrate improved sensitivity in the very window where current testing fails. Additionally, if the proteomics signal is dominated by immunoglobulins, then the model may largely detect the same underlying biology as the intrathecal antibody index rather than providing an independent or earlier indicator. This creates a risk of circularity in the sense that the model’s discriminative features align with the criterion used to label cases. While such a model can still be clinically useful, it does not directly support claims about reducing diagnostic delay. The manuscript would need explicit analyses stratified by symptom duration/antibody titers or inclusion of early/seronegative suspected LNB cases to justify its early-diagnosis framing.\n“Protein signatures were dominated by immunoglobulins (e.g., IGLV3-25, IGLV2-18, FCGBP, IGHM)…”\nThe dominance of immunoglobulins in the CSF signature suggests that a major part of the discriminative signal reflects humoral immune activation, which is closely related to antibody-based diagnostics. This raises a key translational concern: immunoglobulin-driven signatures may share the same timing and persistence issues noted for serology (e.g., delayed rise and long-lived elevation), limiting their ability to resolve early diagnostic uncertainty. The manuscript does not provide evidence that these protein panels appear before standard antibody tests become positive, nor does it quantify performance in early presentations. Moreover, the model’s interpretability via SHAP does not address temporal clinical utility; importance scores can be high even for late-rising markers. Without time-to-diagnosis or early-stage stratification, the study’s strongest clinical motivation remains untested. This weakens the paper’s conclusions about “early” and “rapid” diagnostic improvement.\n“Furthermore, the *B. burgdorferi* s.l.-specific IgG and IgM in blood, poorly predict nervous system involvement.”\nThe manuscript acknowledges that blood immunoglobulins are insufficient for distinguishing CNS involvement, motivating the need for alternative biomarkers. However, the presented CSF signature is immunoglobulin-heavy and the plasma classifier is not shown to overcome the mechanistic limitation highlighted here with a clinically actionable decision threshold and robust validation. If humoral markers dominate, it becomes essential to demonstrate that the proteomics panel adds information beyond existing serology and does so at the relevant clinical decision point. The paper’s evaluation focuses on discrimination against controls/viral meningitis rather than on serologically ambiguous early cases, which are the scenario implied by this statement. As a result, the work does not yet close the gap it identifies. A stronger design would test incremental value over standard serology and evaluate performance in early/seronegative suspected LNB.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "The authors performed data imputation and batch correction on the combined dataset (including both development and validation cohorts) prior to splitting, which introduces data leakage and invalidates the independence of the validation cohort.\n\n\"Samples from the two sites of origin were kept separate in the subsequent analyses to preserve independent cohorts for model development and validation.\"\nThe authors claim to maintain independence between the development and validation cohorts. However, this claim is contradicted by the preprocessing steps described in the methods and implemented in the code, where the datasets were combined before critical processing steps.\n\"The remaining missing values were imputed with a variational autoencoder using the PIMMS software\"\nIn the provided code (`notebook/data_prep.ipynb`), the imputation function `pimms_imputation` is applied to the `df_wide` dataframe, which contains samples from all cohorts. By training the variational autoencoder on the entire dataset, the model learns the data distribution of the validation set, allowing information to leak into the development set. This violates the principle of independent validation and can lead to overoptimistic performance estimates.\n\"Batch correction was executed using combat to overcome potential plate-specific bias on subsequent analyses\"\nSimilarly, the code shows that `batch_correction` was applied to the combined dataset. ComBat adjusts the data based on the mean and variance of the batches across the entire dataset. This aligns the distributions of the development and validation cohorts using information that would not be available in a real-world prospective setting, further contributing to data leakage.\n\"Data leakage is a flaw in machine learning that leads to overoptimistic results. ... we introduce a detailed taxonomy of eight types of leakage, ranging from textbook errors to open research problems.\" [1]\nPreprocessing the entire dataset (imputation, scaling, or batch correction) before splitting into training and test sets is a well-documented form of data leakage. This practice compromises the reproducibility of the results and the generalizability of the model to truly unseen data.\n\nReferences:\n[1] Kapoor, S., & Narayanan, A. (2023). Leakage and the reproducibility crisis in machine-learning-based science. Patterns, 4(9). https://doi.org/10.1016/j.patter.2023.100804", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "The mass spectrometry-based approach fails to detect CXCL13, the most established and accurate biomarker for Lyme neuroborreliosis, resulting in diagnostic performance that is inferior to existing clinical standards.\n\n\"However, the limited detection range inherent to this approach means that certain low-abundance but highly disease-specific proteins, such as CXCL13, may not be captured.\"\nThe authors acknowledge this limitation, but it is a critical flaw for a diagnostic tool intended to improve upon current methods. CXCL13 is widely recognized as a superior biomarker for early LNB diagnosis, often outperforming antibody indices in the early stages of the disease.\n\"In CSF, the classifier distinguished LNB from viral meningitis and controls with AUCs of 0.92 and 0.90, respectively.\"\nWhile an AUC of 0.92 is respectable, it falls short of the diagnostic accuracy reported for CXCL13 assays. A systematic review and meta-analysis has shown that CSF CXCL13 assays can achieve significantly higher sensitivity and specificity.\n\"The overall sensitivity and specificity of CSF CXCL13 were 96% and 95%, respectively.\" [2]\nThis meta-analysis demonstrates that CXCL13 assays offer superior diagnostic performance compared to the results presented in this paper. By failing to capture this key biomarker, the proposed proteomic method represents a step backward in diagnostic accuracy compared to existing, less complex, and potentially cheaper ELISA-based methods.\n\nReferences:\n[2] Rupprecht, T. A., Manz, K. M., Fingerle, V., Lechner, C., & Klein, M. (2018). Diagnostic value of cerebrospinal fluid CXCL13 for acute Lyme neuroborreliosis: a systematic review and meta-analysis. Clinical Microbiology and Infection, 24(12), 1233-1240. https://doi.org/10.1016/j.cmi.2018.04.007", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "The authors claim a \"2-hour\" turnaround time for the diagnosis, which appears to neglect the time required for essential sample preparation steps such as digestion and purification.\n\n\"proteomic test results can be made available with turnaround times of just 2 hours making it highly attractive in real-life clinical settings.\"\nThis claim is a central selling point of the paper but is not supported by the detailed methods. The \"2 hours\" likely refers to the LC-MS instrument time and data analysis, but ignores the significant time needed for sample preparation.\n\"Briefly, 20 µl CSF was were first denatured with 30 µl PreOmics Lysis buffer ... subsequently digested using LysC/trypsin enzyme mix. The resulting peptides were purified using two-gauge SDB-RPS StageTips\"\nEnzymatic digestion with trypsin typically requires several hours to overnight incubation to ensure complete digestion. Even with accelerated protocols, the combination of denaturation, digestion, and manual purification using StageTips would extend the total workflow well beyond 2 hours.\n\"Data acquisition was performed in data-independent analysis (DIA), using 60 samples per day (SPD) gradient\"\nA 60 SPD method implies a cycle time of approximately 24 minutes per sample. While the instrument run is fast, the \"turnaround time\" for a clinical test must include all steps from sample receipt to result. Without a detailed timeline of the sample preparation demonstrating it can be completed in <90 minutes, the \"2-hour\" claim is misleading.\n\"The entire workflow... takes less than 3 hr\" [5]\nThe referenced \"Plasma Proteome Profiling\" method, which serves as the basis for this study, reports a workflow time of roughly 3 hours for sample preparation alone, excluding instrument time. The authors do not provide sufficient details on how they reduced this time to achieve a total turnaround of 2 hours.\n\nReferences:\n[5] Geyer, P. E., et al. (2016). Plasma Proteome Profiling to Assess Human Health and Disease. Cell Systems, 2(3), 185–195. https://doi.org/10.1016/j.cels.2016.02.015", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "Line 202: The number of proteins identified in the plasma samples (median of 268 proteins) is quite low, which is not surprising in the absence of depletion or prefractionation, but only allows the more abundant proteins to be detected. The authors chose to use a very short 8 cm column (probably to increase the number of samples per day). What impact did this length of column have on the number of proteins identified, compared with previous plasma studies in the literature using much longer columns?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "Figure 3A: To be consistent note “Control vs LNB” on the Volcano plot and not “LNB control vs LNB”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "Figure 3B: Line 205 states that 61 proteins are significantly different in VM vs LNB. However, on Figure 3B, a total of 68 proteins (28+33+4+3) are in the corresponding circles. Same remark for the 63 proteins stated Line 206 (LNB vs control), while a total of 69 proteins (33+30+3+3) are in the corresponding circles. What make these differences?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "Line 194 (Fig 3B legend): As seen on Figure 3A and Supplemental Table 2, only 2 proteins (VWF, S100A9) exhibit a fold change larger than 2 in LNB vs control. Similar remark for VM vs LNB with only 6 proteins with a fold change larger than 2. There must be an error in the, since all the significantly proteins are represented, and not only the significant proteins with a fold change larger than 2.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "Line 207: This sentence refers to Figure 3B, not Figure 3C", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "Given that, for plasma, all the significant proteins have been taken into account (and not just those that vary with a fold change larger than 2 as in CSF), are there any consequences for the robustness of a blood-based clinical test?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Human_1|9", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "Line 636 (Mat & Meth): As the MS equipment and the column are different from those used in the cited publications44,45,46, the authors should give more details on LC conditions (e.g. gradient duration) and MS acquisition parameters (or cite additional publications).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "There are issues with this work. The first is the definition of the samples, in particular LNB and controls. LNB was defined based on a first-time positive B. burgdorferi-specific intrathecal antibody test and the ICD-10 code A69 for Borreliosis (which includes all presentations). There is no other information on the clinical presentation or information on pleocytosis.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "The controls were individuals who had no pleocytosis and a negative B. burgdorferi specific intrathecal antibody index after being investigated for suspected LNB. There is no information if these patients had another diagnosis (of Lyme borreliosis or other disease). It is unclear if these controls would not include patients with other presentations of Lyme borreliosis.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "The requirement of a positive IT antibody test anchors the LNB group to this definition. This is reflected on the list of differentially expressed proteins with an absolute log2 fold change larger than 1 provided in in supplementary table 1. I rerun the list using online available tools, and found that 5 of 7 upregulated proteins in LNB compared with viral meningitis (VM) are within the GO CC term immunoglobulin complex GO:0019814, one to IgA immunoglobulin complex, and the other is Fc gamma binding protein. Similar findings are seen compared with controls, where most proteins are related to immunoglobulin complex and related terms. Also shown on the “signature of LNB” where “immunoglobulins were generally upregulated, while proteins involved in innate immune responses and neuroendocrine signaling were relatively downregulated in LNB compared to viral meningitis and controls”. These issues are not discussed in the manuscript.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "The requirement of positive index excludes patients with possible LNB by EFNS criteria who present with pleocytosis and typical clinical presentation. Studies have shown that these patients have a shorter duration of symptoms compared with patients with positive IT index, therefore representing an earlier phase of illness.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "The fact that CXCL13 was not found to be increased in CSF of LNB patients, or to be part of the models is highly problematic. While the explanation that “the limited detection range inherent to this approach means that certain low-abundance but highly disease-specific proteins, such as CXCL13, may not be captured. Given that previous proteomic studies in LNB have also failed to detect CXCL13, this highlights a general challenge in proteomic biomarker discovery rather than a limitation of our study” is possible, it does not recommend the methodology for discovery. CXCL13 is measured in higher levels in CSF in acute LNB than in other neuroinflammatory diseases and may precede antibody production. It has been proposed as both an early diagnostic marker and a marker of treatment response.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "In terms of the ML, twelve models were tested for the CSF data and for plasma data. A LR model was chosen for LNB vs viral meningitis, and an SVC model for LNB vs. controls. No models were developed using the 3 groups. The LR model for LNB vs VM had a MCC of 0.81 on the test set and 0.7 on the validation. For LNB vs controls, the SVC model had an MCC of 0.76 on the test set and 0.63 on the validation. While these are good levels of accuracy, I would disagree with the statement that “Overall, MS-based proteomics coupled with ML demonstrated strong potential as a diagnostic tool for LNB, with particular proteins playing key roles in distinguishing between conditions.” As the LNB group was defined by positive IT index, this would have a MCC of 1. It is also highly likely that Lyme serological test would also have a higher MCC, and possibly CXCL13.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "The plasma analysis showed that VM patients and controls had higher immunoglobulin levels than LNB patients. These are highly unexpected and unexplained results, particularly comparing with controls. An explanation for these findings, including technical issues need to be provided.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "The ML model for plasma focused only in differentiating between controls and LNB. The SVC model chosen had a MCC of 0.83 on the test set, but only 0.48 in the validation set.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "The authors stated that the model identified acrodermatitis chronica atrophicans and erythema migrans compared to post-treatment Lyme disease syndrome and viral meningitis. However, little detailed information is given regarding the individual presentations, the numbers are small for some, and no comparison is done to available methodologies.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Human_2|10", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "Another difficulty is the possible variation caused by age differences in the groups. While there is no analysis of the differences, by the information provided (median age and IQR) is possible that there are significant differences between the groups. This is mentioned only in brief in the discussion.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Human_2|11", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "The discussion highly overrepresents the results, and downplays the problems and limitations of the study. Examples include statements like “MS-based proteomics can accurately differentiate patients with LNB from patients with viral meningitis and non-LNB controls”, “observed a high level of diagnostic accuracy in plasma, highlighting the potential of blood-based proteomics as a clinically valuable tool” and “In conclusion, our findings demonstrate that MS-based proteomics can accurately distinguish LNB from controls in both CSF and plasma”. The results do not support these statements. It is likely that the models would not perform any better than current antibody-based assays.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Human_2|12", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "Figures are difficult to read due to small print, particularly figures 1 and 3. There are label overlaps in Figure 1 and supplementary figures 2 and 3.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "The authors should be praised for having a diverse sample set including non-Lyme diseases. For the viral meningitis cases, what assay was used for pathogen detection. Should state the assay. For example if BioFire FilmArray ME Panel was used, the HSV target has some limitations. In clinical practice, HSV testing may need to be tested on a separate assay, due to concerns on assay performance.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "On the same topic, the authors noted that a lot of the signal detected MS in CSF were immunoglobulins. Can the authors suggest, perhaps in the Discussion Section, how other diseases such as multiple sclerosis which has unique immunoglobin profiles in CSF, would impact the assay performance?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "Can the authors comment on how long the test takes? This helps discuss how translatable it is for real world practice if this is ever adopted for routine clinical testing. I see a comment of 2 hours in line 90. Is this true, in the context of total testing time, not just the mass spec phase and/or informatics. What is the turnaround time from sample to fully verified result?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "For machine learning (ML), how did the authors select the 12 models? At least logistic regression (LR) and support vector machine (SVM) was used. Was the use of LR and SVM based on a priori experience, familiarity, or other? The reason is there's been some studies showing an agnostic approach using a range of ML techniques could identify better models. Automated ML software has this advantage, although, it won't replace data scientists, some studies using MALDI-TOF-MS for infectious disease host responses found automated ML systems finding better models compared.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "Often, ML models should be further validated with a tertiary dataset, which helps with generalization. Can the authors comment on how the results from this initial study are likely to be translated to samples from another location? For instance, disease prevalence is a limitation here as the authors noted for viral meningitis. If a new dataset were to have a higher prevalence of different diseases, could this alter the results?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|55|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb55", "comment": "For ML models, are there any other variables used to evaluate the model such as F-statistic and/or Brier Scores?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|56|Claude|2", "source": "prb", "split": "test", "paper_id": "prb56", "comment": "The clinical validation exclusively tested samples from liver transplant patients without including healthy controls, making it impossible to establish the bactosensor's specificity—the ability to correctly identify samples from individuals without elevated bile salts.\n\n\"Serum samples were consecutively collected from hospitalized or ambulatory liver transplant patients at the Hepatology and Liver Transplantation Unit, Hôpital Saint-Eloi in Montpellier (France)\"\nThe study design includes only liver transplant patients without healthy control subjects. This is a fundamental limitation because diagnostic specificity cannot be determined without testing negative samples from individuals known to have normal bile salt levels. Studies evaluating bile acids as liver biomarkers typically include healthy control groups—for example, Luo et al. [[4]](#citation-4) included \"331 subjects\" comprising both \"healthy human subjects and subjects with liver impairments\" to properly evaluate diagnostic ROC curves with sensitivity and specificity calculations.\n\"A complete hepatic check-up was performed, and serum bile salts were also measured (Supplementary Tables 3–5 for clinical data).\"\nThe supplementary clinical data (Tables S2-S5) confirms that all 21 samples came from transplant patients with various underlying conditions. Without negative controls, the paper cannot claim the bactosensor demonstrates diagnostic utility—it can only claim analytical correlation with existing enzymatic assays. The recent study on serum bile acids as NAFLD biomarkers by Elhassaneen et al. [[5]](#citation-5) demonstrated AUC values and cutoff determinations specifically by comparing patient groups to \"healthy controls,\" achieving diagnostic performance metrics like \"96% specificity and 74.7% sensitivity.\"\n\nReferences:\n[4] [Luo, L. et al. Assessment of serum bile acid profiles as biomarkers of liver injury and liver disease in humans. PLoS One 13, e0193824 (2018)](https://journals.plos.org/plosone/article?id=10.1371/journal.pone.0193824)\n[5] [Exploring serum bile acids as potential noninvasive biomarkers for NAFLD - Egyptian Liver Journal (2024)](https://link.springer.com/article/10.1186/s43066-024-00378-9)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|56|Claude|3", "source": "prb", "split": "test", "paper_id": "prb56", "comment": "The paper acknowledges that several serum samples showed \"low or negative responses\" potentially due to \"differential matrix effects arising in samples from different patients,\" but does not characterize, quantify, or correct for these effects, undermining the reliability of the assay in real clinical applications.\n\n\"We observed that our bactosensor had relatively low or negative responses to several serum samples (Fig. 5b and Supplementary Fig. 16). This behavior may be due to differential matrix effects arising in samples from different patients.\"\nThe paper acknowledges that matrix effects cause variable and even negative responses but provides no systematic investigation or correction strategy. According to a recent study using similar TcpPH-EMeRALD biosensors in fecal samples, \"matrix effects varied significantly from patient to patient\" and such effects could \"up to 3.6-fold\" change biosensor output [[6]](#citation-6). The authors' own subsequent work in Frontiers in Bioengineering found \"significant inhibitory matrix effects of feces on the bacterial biosensors tested\" including the TcpP/TcpH system [[7]](#citation-7). This variability is particularly concerning when negative responses are observed (Table S4 shows patient #21 with bactosensor reading of -0.08), as this could lead to false negatives in diagnostic applications.\n\"Large-scale analysis of clinical samples chemical composition coupled with close monitoring of the diet and medical treatments for each patient could help identify the causes of this effect.\"\nWhile the authors propose future investigation, the current data cannot be reliably interpreted without understanding the source of patient-to-patient variability. The high correlation (r=0.908) is driven largely by three outlier patients with very high bile salt concentrations; removing these could substantially change the correlation. Without proper matrix effect characterization, the claimed diagnostic reliability is not adequately supported by the evidence presented.\n\nReferences:\n[6] [A Screening Assay for Bile Acid-Transforming Microorganisms - Biosensors (2024)](https://pmc.ncbi.nlm.nih.gov/articles/PMC12649884/)\n[7] [Zúñiga, A. et al. A rapid and standardized workflow for functional assessment of bacterial biosensors in fecal samples. Front. Bioeng. Biotechnol. (2022)](https://www.frontiersin.org/journals/bioengineering-and-biotechnology/articles/10.3389/fbioe.2022.859600/full)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|56|Claude|5", "source": "prb", "split": "test", "paper_id": "prb56", "comment": "The paper reports that changing from GFP to LacZ reporter \"slightly shifted\" the bile salt specificity profile from TCA to GCDCA without providing mechanistic explanation, which creates uncertainty about which bile salt species the clinical assay is actually detecting in patient serum samples that contain multiple bile salt types.\n\n\"Similarly to the biosensor equipped with a GFP output, the bile salt specificity profile of the TcpP18-LacZ system was slightly shifted from TCA to GCDCA (Fig. 4b, Supplementary Fig. 13).\"\nThe shift in specificity profile is acknowledged but unexplained. Since patient serum samples contain complex mixtures of multiple bile salt species [[10]](#citation-10), understanding which specific bile salt(s) the bactosensor preferentially detects is critical for clinical interpretation. The TcpP18-LacZ sensor shows peak response to GCDCA rather than TCA, yet the clinical validation correlates bactosensor output with total bile salt measurements (which include all bile acid species). This mismatch between the sensor's apparent specificity and the clinical reference measurement adds uncertainty to the diagnostic interpretation.\n\"Due to the link between primary bile salts and liver diseases, we selected the TcpP/TcpH system to develop a bile salt bactosensor for medical diagnosis.\"\nThe rationale for selecting TcpP/TcpH was its preference for primary bile salts, particularly TCA. However, the final clinical sensor (TcpP18-LacZ) shows shifted specificity toward GCDCA, and the implications of this shift for clinical diagnosis are not discussed. Since different liver pathologies may have distinct bile salt profiles [[11]](#citation-11), understanding the exact detection profile is essential for proper diagnostic application, particularly if the bactosensor is to be used for monitoring specific conditions like acute cellular rejection.\n\nReferences:\n[10] [Liu, Y. et al. Detection technologies and metabolic profiling of bile acids: a comprehensive review. Lipids Health Dis. 17, 121 (2018)](https://link.springer.com/article/10.1186/s12944-018-0774-9)\n[11] [Use of bile acids as potential markers of liver dysfunction in humans - PMC (2021)](https://pmc.ncbi.nlm.nih.gov/articles/PMC8519223/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|56|GPT|3", "source": "prb", "split": "test", "paper_id": "prb56", "comment": "This paper reports improvements in “limit-of-detection (LOD)” using EC50 values without defining or calculating LOD in the standard analytical sense, which makes the central sensitivity/LOD claims quantitatively unreliable.\n\n\"The 3.3-fold difference in LOD between V18 and V22 (EC50 from 28.3 to 92.5 µM, Table 1) indicated the broad range of sensitivity engineering obtained by mutating the loop region of the TcpP sensing module.\"\nThis sentence explicitly equates LOD with EC50, but EC50 is a mid-response potency metric (the concentration producing half-maximal response), not the lowest detectable concentration above a blank/noise threshold. Conflating these quantities can materially distort interpretation: a lower EC50 does not guarantee that the assay can reliably distinguish very low concentrations from the blank, especially if background and variance also increase. The paper also uses LOD as a selection criterion across promoter variants and engineered receptors, so this definitional issue propagates through the performance narrative. Standard practice would require specifying how baseline signal and variability were quantified and how the LOD threshold was chosen. Without that, the reported “LOD improvements” cannot be compared fairly to other biosensors or clinical chemistry assays. This is a major methodological weakness because “LOD” is central to the claimed engineering advance.\n\"| # Variant | Sequence | EC50 (µM) | Response EC50 (RPU) | Max fold change |\"\nThe table itself is labeled in terms of EC50, reinforcing that the quantitative parameter estimated for variants is EC50 rather than an analytically defined LOD. If the authors intended EC50 as a proxy for sensitivity, that should be stated consistently and not relabeled as LOD, because readers interpret “LOD” as a detection-threshold concept. Moreover, EC50 estimation typically depends on the choice of model (e.g., Hill function), fit procedure, and weighting, none of which are described here; this further complicates the reliability of the derived values as a substitute for LOD. Because LOD is often computed from blank statistics and calibration slope, a table of EC50 values does not provide the information needed to reproduce or verify the claimed LOD changes. The “Max fold change” column also shows that improved EC50 can come with reduced dynamic range, highlighting why a proper LOD calculation (incorporating noise) matters. Overall, the quantitative reporting does not support a defensible LOD claim.\n\"The limit of detection, expressed as the concentration, \\(c_{\\rm{L}}\\), or the quantity, \\(q_{\\rm{L}}\\), is derived from the smallest measure, \\(x_{\\rm{L}}\\), that can be detected with reasonable certainty ... \\(x_{\\rm{L}}=\\overline{x}_{\\rm{bi}}+k\\ s_{\\rm{bi}}\\) ...\" [[3]](#ref3)\nThis standard definition makes clear that LOD is derived from blank measurements and their variability, not from the concentration producing half-maximal response. Applying this definition to the paper’s context would require reporting the blank (no bile acid) signal distribution for the assay readout, a chosen confidence factor k, and an explicit mapping from signal to concentration. The manuscript does discuss background increases in the colorimetric assay (“background signal also increased”), which further emphasizes that noise/blank behavior is relevant to LOD. Because the paper instead reports EC50 as “LOD,” it is unclear whether the assay can reliably detect concentrations near the lower end of the claimed clinically relevant range. This affects cross-study comparability and practical deployment decisions, especially for point-of-care monitoring. The mismatch between the definition and the reported metric is therefore a significant problem for the paper’s key performance claims.\n\nReferences:\n[3] <a id=\"ref3\"></a>[IUPAC Gold Book: Limit of detection in analysis (L03540).](https://goldbook.iupac.org/terms/view/L03540)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|56|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb56", "comment": "The study fails to include healthy control subjects to establish a baseline specificity and does not adequately address potential interference from serum components or drugs, which is critical for validating a clinical diagnostic tool.\n\n\"We tested our bactosensor in clinical 21 serum samples from liver transplantation patients\"\nThe study only evaluates the sensor on liver transplant patients, who are typically on complex medication regimens (e.g., immunosuppressants). The absence of healthy controls makes it impossible to assess the false-positive rate or the baseline signal in a normal serum matrix, which is a fundamental requirement for diagnostic validation [1].\n\"For the clinical sample assay, serum samples were heat-inactivated by incubation in a 56℃ water bath for 30 mins.\"\nWhile heat inactivation is used, the authors do not investigate whether this treatment effectively mitigates interference from serum proteins like albumin, which binds bile salts with high affinity [2]. In physiological conditions, a significant fraction of bile salts is protein-bound. The assay might be measuring a mix of free and released bile salts in a way that doesn't reflect the pathological \"free\" bile salt levels, or conversely, residual albumin might buffer the bile salts, affecting the sensor's apparent sensitivity.\n\"Patient 7... hospital bile salt: 19... Bile salt (sigma kit): 76.22\" (from Supplementary Table 4)\nThere are major discrepancies between the hospital's clinical measurement and the commercial kit used as a reference (e.g., a 4-fold difference for Patient 7). This suggests significant matrix effects or methodological issues in quantifying bile salts in these samples, which the paper fails to resolve or discuss.\n\nReferences:\n[1] Pepe, M. S. et al. Phases of biomarker development for early detection of cancer. *J. Natl. Cancer Inst.* **93**, 1054–1061 (2001). https://academic.oup.com/jnci/article/93/14/1054/2520276\n[2] Roda, A. et al. Serum bile acids in hepatobiliary disease. *J. Clin. Pathol.* **26**, 979 (1973). https://jcp.bmj.com/content/26/12/979", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|56|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb56", "comment": "The authors also note that other bile salt sensors measure total bile salts but theirs does only primary bile salts. That may be true, but the challenge of what they are trying to do becomes evident with patients like #17, who have high bile salt levels but who do not get a big response from their sensor. It seems possible that their sensor’s profile of what they can detect does not align with what is in that patient, which becomes a potential issue with their non-specific approach to primary bile salts.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|56|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb56", "comment": "And arguments about whether some things are overstated... like when the authors conclude a response with “To conclude, as of today we don’t see any “other method” capable of providing deep mutational exploration, high-throughput screening, and a functional in-cellulo assay to explore sequence-function relationships of bacterial sensing modules.” Sure, one can do those things with EMeRALD. Or with a natural transcription factor. Or with any other engineered transcription factor. There is just nothing that is unique to EMeRALD there. A “platform” that includes collectively requiring rational protein evolution, deep sequencing, etc etc, just does not seem to be “scalable” or “rapid” or widely adoptable.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|57|Claude|4", "source": "prb", "split": "test", "paper_id": "prb57", "comment": "The in vivo experiments use plasmid-based overexpression systems for the coat protein and slncRNA, which are known to cause aggregation artifacts with MS2/PP7 systems, but the paper does not adequately address or control for these known issues.\n\n\"We found that cells containing the multicopy plasmid frequently present puncta in at least one of the poles, while cells containing the single copy generally show between zero and one punctum (Figure. 4d).\"\nThe observation that multicopy plasmids yield more polar puncta than single-copy vectors is consistent with known overexpression artifacts described in the MS2/PP7 literature. Garcia & Parker (2015) and subsequent studies showed that overexpression of MS2-tagged mRNAs leads to accumulation of granules and fragments that co-localize with P-bodies, which are typically located at cell poles in bacteria [[3]](#citation-3).\n\"BL21-DE3 cells expressing the two plasmid system (single copy plasmid containing the binding sites array, and a multicopy plasmid containing the fluorescent protein fused to an RNA binding protein)\"\nThe use of a multicopy plasmid for expressing the fluorescent coat protein could result in substantial overexpression. Studies have shown that overexpression of coat proteins can lead to their accumulation independently of RNA, potentially forming aggregates that could be mistaken for RNA-containing granules [[4]](#citation-4).\n\"All told, the evidence we present here strongly suggests that the use of plasmid-based overexpression systems to localize mRNAs... can give a false impression of global mRNA protection and, in some cases, probably altered mRNA localization.\" [[3]](#citation-3)\nThis quote from Haimovich et al. (2016) directly addresses the issue of MS2 system artifacts when using overexpression. The paper under review does not perform the control experiments recommended by this and other studies, such as comparing with endogenously tagged constructs or verifying that observed structures are not P-body associated aggregates.\n\"To check that this condensation was hairpin dependent, we tested whether a control RNA (of the same length and GC content as PCP-8x) containing no designed hairpin condensed either on its own or in the presence of tdPCP-mCherry forms granules. In both cases, no condensates were detected in either the 488 nm or 585 nm channels (data not shown).\"\nThe critical negative control data showing that non-hairpin RNA does not form granules is mentioned but not shown. This key experiment supporting the specificity of granule formation should be included in the main figures or supplementary material, as readers cannot evaluate this claim without seeing the data.\n\nReferences:\n[3] [Haimovich, G., Zabezhinsky, D., Haas, B., et al. Use of the MS2 aptamer and coat protein for RNA localization in yeast: A response to \"MS2 coat proteins bound to yeast mRNAs block 5′ to 3′ degradation and trap mRNA decay products\". RNA 22, 660–666 (2016)](https://pmc.ncbi.nlm.nih.gov/articles/PMC4836641/)\n[4] [Tutucci, E., Vera, M., Biswas, J., Garcia, J., Parker, R. & Singer, R. H. An improved MS2 system for accurate reporting of the mRNA life cycle. Nature Methods 15, 81–89 (2018)](https://www.nature.com/articles/nmeth.4502)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|57|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb57", "comment": "The paper's central method for detecting \"bursts\" of fluorescence intensity is statistically flawed and likely detects artifacts of the data smoothing process rather than genuine biological events.\n\n`window_span = 13; % Moving average filter window span (Required to reduce signal noise)`\nThe authors apply a moving average filter with a window size of 13 points to the raw fluorescence data. Smoothing random noise with a moving average introduces autocorrelation, creating artificial trends and cycles with a characteristic length related to the window size, a phenomenon known as the Slutsky-Yule effect [1, 2].\n`threshold = ceil(-probability/log2(posChance));`\nThe burst detection algorithm calculates a threshold for the length of monotonic segments based on the probability of a positive step (`posChance`). For random noise, `posChance` is approximately 0.5, and with the authors' chosen `probability` parameter of 12, the threshold becomes `ceil(-12/log2(0.5)) = 12`.\n`points = lengths>threshold;`\nThe algorithm identifies \"bursts\" as runs of monotonic increase or decrease longer than this threshold (12 points). Since the smoothing window (13 points) introduces correlations of approximately the same length, runs of length > 12 are statistically expected to occur frequently even in pure noise.\n\"For the granules, this rate (~5 minutes) is two orders of magnitude above the typical rate observed in liquid phase separated condensates\"\nThe reported rate of bursts (~5 minutes, or 30 time points) is consistent with the timescale of artifacts generated by the smoothing window (13 points) and the detection threshold (12 points). The \"bursts\" are likely spurious fluctuations resulting from the data processing pipeline rather than physical shedding or addition events.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|57|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb57", "comment": "The classification of the granules as \"solid-like\" or \"gel-like\" is not supported by standard biophysical characterization methods and relies heavily on the flawed burst analysis.\n\n\"For the granules, this rate (~5 minutes) is two orders of magnitude above the typical rate observed in liquid phase separated condensates24, but is in line with the measurements performed on RNA gels by Vale et. al.11, providing additional confirmation that the SRNP granules are gel-like particles.\"\nThe authors use the \"burst rate\" derived from their flawed analysis to argue for a solid-like state. Since the burst rate is likely an artifact of the smoothing parameters, it cannot serve as evidence for the material state of the granules.\n\"The RNA granules presented features associated with liquid-solid phase transition systems: a lack of internal mobility, virtually no fusion events\"\nWhile the authors mention \"virtually no fusion events,\" they do not provide quantitative data or time-lapse imaging of fusion attempts to substantiate this claim. Standard guidelines for characterizing phase-separated condensates recommend Fluorescence Recovery After Photobleaching (FRAP) to quantify internal mobility and fusion assays to determine material properties [4].\n\"The RNA granules presented features associated with liquid-solid phase transition systems... These characteristics helped establish the granules as physical solids.\" [3]\nThe cited work by Jain and Vale [3] rigorously established the solid-like nature of RNA granules using FRAP and fusion assays. The current paper lacks comparable biophysical evidence and relies instead on the questionable \"burst\" dynamics.\n\nReferences:\n[3] Jain, A., & Vale, R. D. (2017). RNA phase transitions in repeat expansion disorders. *Nature*, 546(7657), 243-247. https://doi.org/10.1038/nature22386\n[4] Alberti, S., Saha, S., Woodruff, J. B., Franzmann, T. M., Wang, J., & Hyman, A. A. (2018). A User's Guide for Phase Separation Assays with Purified Proteins. *Journal of Molecular Biology*, 430(23), 4806-4820. https://doi.org/10.1016/j.jmb.2018.06.038", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|57|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb57", "comment": "The proposed \"capacitor\" model, which posits that granules function as programmable storage devices for proteins, is an over-interpretation of the fluorescence intensity fluctuations and lacks direct experimental verification.\n\n\"Temporal tracking of individual SRNP granules reveals that granules function as protein capacitors\"\nThis major conclusion is based entirely on the interpretation of fluorescence intensity fluctuations as discrete \"charging\" and \"discharging\" events. As established in Item 1, these fluctuations are likely statistical artifacts.\n\"Consequently, our granules constitute a genetically encoded storage compartment for protein and RNA with a programmable controlled release profile that is determined by the number of hairpins encoded into the RNA.\"\nThe claim of \"programmable controlled release\" assumes that the \"bursts\" represent controlled shedding of complexes. Without validating that these bursts correspond to single-molecule events (e.g., using single-molecule tracking or stepwise photobleaching), the \"capacitor\" mechanism remains speculative.\n\"Assuming an interpretation that fluorescent burst events correspond to insertion and shedding events of slncRNA-CP complexes into or out of the synthetic granules\"\nThe authors explicitly state this is an assumption. However, they proceed to build their entire biological model on this unverified assumption, which is undermined by the statistical flaws in the detection method.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|57|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb57", "comment": "The *in vivo* data does not sufficiently distinguish the reported granules from non-specific protein aggregates or inclusion bodies, which weakens the claim of a functional \"phase-separated\" compartment.\n\n\"This observation is consistent with the phenomenon of nucleoid exclusion, which has been reported for other large protein aggregates and phase separated structures in bacteria\"\nThe authors acknowledge that nucleoid exclusion is a common feature of protein aggregates [5]. Therefore, this observation does not specifically support the claim that the granules are functional, phase-separated \"capacitors\" rather than misfolded protein aggregates (inclusion bodies).\n\"In the case here, the granules can be used not only to increase levels of a protein of choice by nearly an order of magnitude... but may also provide a mechanism to increase the cell's ability to survive when a harsh or stressful environment is encountered.\"\nThe persistence of granules in stationary phase and their dissolution upon dilution is also characteristic of inclusion bodies, which can be reversible. The paper does not provide evidence (such as functionality assays of the stored protein or specific release mechanisms) to distinguish the \"capacitor\" function from simple reversible aggregation.\n\nReferences:\n[5] Neeli-Venkata, R., Martikainen, A., Gupta, A., Gonçalves, N., Fonseca, J., & Ribeiro, A. S. (2016). Robustness of the Process of Nucleoid Exclusion of Protein Aggregates in Escherichia coli. *Journal of Bacteriology*, 198(6), 898-906. https://doi.org/10.1128/JB.00848-15", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|57|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb57", "comment": "In figure 1b the authors claim that the longer sIncRNA molecules exhibit larger structures. It is clear by eye that the number of the structures is higher however it is difficult to notice the size increase. Could the author do measurements of the different granule sizes in the different conditions and perform statistical analyses to prove their idea?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|57|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb57", "comment": "In the same figure, did the author use higher concentrations of PCP3x to check if it is able to form granules?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|57|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb57", "comment": "In figure 1c are the plots normalized to the amount of incorporated fluorescent U? the longer the size of the fragment, the more fluorescent uracils are incorporated and the higher the signal is.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|57|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb57", "comment": "The interpretation of the results in figure 1d and 1e should be more developed and correlated with the normalization if fig 2c.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|57|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb57", "comment": "In figure 2b, the authors should show the control RNA experiments. It is exactly the negative control that is missing for this experiment. This could help understanding/proving that the hairpins are the important structures and not any RNA with its RNA binding Protein are able to form granules", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|57|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb57", "comment": "In figure 2b, could the authors use any other RNA binding protein to demonstrate that this observation is due to the specificity of PCP and not any other physical properties of RBPs.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|57|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb57", "comment": "In figure 2c and 2d the same normalization as in figure 1 should be used.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|57|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb57", "comment": "In figure 2e a titration experiment could be of great interest to understand the dynamics of the granules. Authors can use non fluorescent probe competitors at different concentration to check when the proteins are displaced.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|57|Human_1|9", "source": "prb", "split": "test", "paper_id": "prb57", "comment": "Another competition assay can be used. Once the granules are formed, authors can incubate with different probe sizes (different labels) to check the proteins displacement etc.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|57|Human_1|10", "source": "prb", "split": "test", "paper_id": "prb57", "comment": "In figure 3b, authors can use RNase to prove their hypothesis of the RNA degradation and the bias towards negative bursts.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|57|Human_1|11", "source": "prb", "split": "test", "paper_id": "prb57", "comment": "In figure 3e, 3f and 3g would it be possible to perform the competition/titration experiment?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|57|Human_1|12", "source": "prb", "split": "test", "paper_id": "prb57", "comment": "In figure 4b a negative control should be used to prove the specificity of the observation.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|57|Human_1|13", "source": "prb", "split": "test", "paper_id": "prb57", "comment": "The images in figure 4b, 4c and 4e are very low quality.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|57|Human_1|14", "source": "prb", "split": "test", "paper_id": "prb57", "comment": "Can the authors extend the discussion about the granule formation and the dynamics of the granules in different biological process and diseases.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|57|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb57", "comment": "In the RNA granule experiment presented in figure 1, in vitro transcribed RNA was resuspended in 'granule buffer' containing high salt, magnesium and PEG. Of note, under such buffer conditions and at 8.5nM concentration, RNA could form secondary structures (intramolecular) at room temperature, sufficient to create an array of RNA-RNA interactions (intermolecular) to lead to formation of RNA oligomers that will be of detectable size and interpreted as phase separated entities. It is plausible that nucleic acids such as RNA, do not 'condensate' but readily form hydrogen-bonds with stretches of complementary nucleic acids. Therefore, addition of controls such as a no-hairpin containing RNA should eliminate experimental artifacts.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|57|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb57", "comment": "In addition, it is not clear whether different sIcnRNA designs match or differ in their fluorophore-tagged Uracil contents, which would directly affect overall fluorescence intensity. If sIcnRNA designs with different numbers of hairpin motifs vary in their Uracil contents, it is important to know their background levels. Images in Figure 1b suggest that the background fluorescence intensity among the different sIcnRNAs is variable.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|57|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb57", "comment": "Without knowing a priori the number of molecules in each granule, it becomes difficult to ascertain the relationship between fluorescence intensity and the number of hairpins. Also the nonlinearity of this relationship cannot be assigned to the number of ~hairpins as each granule may have varying numbers of RNA molecules, confounded by longer RNA molecules oligomerizing more than short RNA.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|57|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb57", "comment": "In the RNA-protein granule experiments, it is not clear how much is an RNA-mediated process or a protein-driven process- the outcome of granular formation would be affected by both components. Therefore, a negative control for each component may help quantify the relative contributions. For example, sIcnRNA without hairpin motifs and non-binding proteins such mCherry may help understand the process better. Another question is whether equal molar amounts of sIcnRNAs have been used. As the concentration of RNA component is an important parameter, it would be helpful if the same molar amounts are used. Again, the lack of these controls makes it hard to interpret whether the imaged particles are brighter due to condensation or simple binding.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|57|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb57", "comment": "In addition, some scale bars are not provided (in Figure 1b and Figure 2e), and this makes it difficult to gauge the homogeneity or uniformity of the particles, in terms of their size and shape. For example, in Figure 2f some granules appear to be bigger than others. This may be due to a variety of factors such as those enumerated above.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|57|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb57", "comment": "In cells, PP7 stem-loops and PCP have been used to visualize RNA at single molecule resolution. This is because multimerizing PP7 (24x) brings together up to 24x fluorescent PCP per RNA so that it is now bright enough for detection. When expressed in bacteria, the reason why co-expression of RNA and protein (tdPCP-mCherry) appears brighter is because the RNA behaves as a scaffold to bring PCPs within a diffraction-limited spot which now fluoresces brighter than the unbound and freely diffusing tdPCP-mCherry in the background. When the protein is expressed by itself or along with control sncRNA lacking hairpin motifs, there should not be an instance where the protein accumulates within a diffraction-limited spot inside the cell as shown in Figure 4c. The quantification of this negative control experiment would be helpful in convincing the reader.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|57|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb57", "comment": "The use of measurements from real-time imaging of the fluorescent granules to study kinetics of granule formation driven by the ratio of stem loops and binding proteins and the capacitor model for the shedding is an inspired approach. The interpretation of their results and its implications in the Discussion need clarification. For instance, in line 229-230 the authors suggest that RNA degradation might contribute to the bias toward shedding of sncRNA (\"...the amplitude bias towards negative events is consistent with RNA degradation and lack of transcription within the in vitro suspension, leading to a net shedding of sncRNA molecules out of the granules over time\"). However, in the Discussion the authors then suggest that this system can potentially be \"utilized as a programmable controlled release mechanism in suitable biological settings\" (lines 422-423). The authors need to consider the impact of equilibrium and non-equilibrium models in the context of the shedding. Capacitors eventually run down unless they are in a periodically charged environment.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|58|Claude|1", "source": "prb", "split": "test", "paper_id": "prb58", "comment": "The paper claims that mucosal vaccination may \"provide protection against infection and minimise viral spread\" but fails to measure immunity or viral loads in the upper respiratory tract (URT), where SARS-CoV-2 infection initiates. All mucosal immunity assessments (IgA, neutralizing antibodies) were performed using broncho-alveolar lavage fluid (BALF), which represents the lower respiratory tract. No nasal wash, nasal turbinate samples, or tracheal immunity data were collected to support claims about preventing infection at the primary site of viral entry.\n\n\"Strikingly, anti-Spike IgA was only detected in the serum or BALF of i.n immunized mice, where it was present at very high titres.\"\nThe authors report IgA only in serum and BALF, with no mention of nasal IgA or nasal wash samples. BALF represents the lower respiratory tract (alveolar space), not the nasal passages where SARS-CoV-2 infection initiates. Since SARS-CoV-2 first infects the upper airway epithelium, demonstrating mucosal immunity at this site is essential for claims about preventing infection and transmission. The absence of URT sampling represents a significant methodological gap in supporting the paper's central claims about mucosal protection.\n\"Consistent with the substantial antibody response generated by Pam₂Cys Spike, vaccination by either route induced sterilizing protection with no virus detected in the lung tissue at day 7 post infection\"\nThe sterilizing immunity claimed is demonstrated only in lung tissue at a single timepoint. No viral loads were measured in the nasal turbinates or trachea. Without URT viral load data, it is impossible to conclude whether the vaccine prevents initial infection and viral shedding from the nose, which are critical for transmission prevention. The paper's Discussion acknowledges this gap by stating future studies require assessment \"in the URT such as the nasal mucosa and trachea.\"\n\"Since SARS-CoV-2 infection initially occurs in the URT, protecting the URT is hypothesized to control further virus spread to the lower respiratory tract, thereby preventing severe disease, and limit virus transmission.\" [[1]](#citation-1)\nThis recent study emphasizes that URT protection is crucial for preventing transmission and controlling viral spread. The standard methodology for mucosal vaccine studies now includes assessment of nasal turbinate samples and nasal-associated lymphoid tissue (NALT). The reviewed paper's lack of URT sampling fails to meet this contemporary standard for demonstrating mucosal protection against respiratory pathogens.\n\"Studies conducted in various preclinical animal models indicated that mucosal vaccination could reduce or completely prevent virus transmission... Mucosal immunization of primary contact hamsters with ChAd-CoV-2-S reduced SARS-CoV-2 in the upper and lower respiratory tract\" [[1]](#citation-1)\nOther mucosal vaccine studies explicitly measure and report viral loads in both URT and LRT compartments to support transmission prevention claims. The absence of such measurements in the reviewed paper means the conclusions about preventing infection and transmission are not directly supported by the experimental data presented.\n\nReferences:\n[1] [Intranasal booster induces durable mucosal immunity against SARS-CoV-2. Nature Scientific Reports (2025).](https://www.nature.com/articles/s41598-025-06880-3)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|58|Claude|4", "source": "prb", "split": "test", "paper_id": "prb58", "comment": "The paper reports that 40% of mice receiving intranasal Pam₂Cys alone (without Spike protein) were protected from weight loss and had no detectable lung virus. This substantial antigen-independent protection effect confounds the interpretation of protection data in the Pam₂Cys Spike groups, making it difficult to attribute the observed complete protection specifically to adaptive immunity against the Spike protein versus innate immune activation by the adjuvant.\n\n\"In contrast, mice immunized s.c with Pam₂Cys adjuvant only had no protection, however, 40% of mice receiving Pam₂Cys i.n notably did not lose weight or show clinical indicators of disease\"\nThe 40% protection rate in the Pam₂Cys-alone intranasal group is remarkably high for a control that contains no viral antigen. This suggests that TLR2 activation in the respiratory tract alone provides significant non-specific protection. When the Pam₂Cys Spike intranasal group shows 100% protection, it becomes unclear how much of this protection is attributable to Spike-specific adaptive immunity versus the substantial innate immune priming effect of the adjuvant.\n\"Intriguingly, 60% of mice receiving Pam₂Cys i.n also had no detectable virus in lung tissue\"\nThe sterilizing immunity observed in 60% of mice receiving only the adjuvant intranasally further complicates interpretation. If the adjuvant alone can eliminate virus from the lungs in the majority of mice, the added benefit of Spike protein cannot be easily quantified from the presented data. This fundamentally challenges the claim that \"potent\" Spike-specific responses are driving protection.\n\"Of interest, SARS-CoV-2 challenge following parenteral and mucosal immunization revealed that the delivery of the adjuvant Pam₂Cys by the i.n, but not the s.c route, resulted in a partial protective effect\"\nThe authors acknowledge this phenomenon but frame it as an interesting observation rather than as a confounding factor. The non-specific protection from mucosal Pam₂Cys delivery means that appropriate experimental design would require additional controls (e.g., mucosal delivery of an irrelevant antigen with Pam₂Cys) to properly attribute protection to Spike-specific immunity.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|58|GPT|3", "source": "prb", "split": "test", "paper_id": "prb58", "comment": "This paper’s interpretation that protection is primarily vaccine antigen-specific is not sufficiently supported, because the intranasal adjuvant-only control shows substantial protection and undetectable lung virus in many animals, making it unclear how much of the protection phenotype is attributable to Spike-specific adaptive immunity versus Pam₂Cys-driven antigen-independent mechanisms.\n\n\"In contrast, mice immunized s.c with Pam₂Cys adjuvant only had no protection, however, 40% of mice receiving Pam₂Cys i.n notably did not lose weight or show clinical indicators of disease.\" \nThis observation indicates that route-matched adjuvant alone (Pam₂Cys i.n) can materially alter the clinical phenotype after SARS-CoV-2 challenge. Because the protective readouts (weight loss, clinical score) are central to the paper’s efficacy claim, any strong adjuvant-only effect complicates attribution of protection to Spike-specific immunity. The manuscript does not provide mechanistic experiments (e.g., antibody transfer, T cell depletion, or delaying challenge to beyond innate-priming windows) to separate trained/primed innate effects from adaptive effects. With only n=5 per group, a 40% “protected” fraction also has wide uncertainty, reinforcing that mechanistic resolution is needed. Without disentangling these mechanisms, the study’s causal story about vaccine-induced adaptive immunity driving protection is incomplete.\n\"Intriguingly, 60% of mice receiving Pam₂Cys i.n also had no detectable virus in lung tissue.\" \nThis is a striking finding because undetectable lung PFU is the same endpoint used to support “sterilizing” protection for the antigen-containing vaccine groups. If an adjuvant-only intranasal regimen can yield the same terminal lung virology endpoint in most animals, then that endpoint alone cannot uniquely evidence antigen-specific sterilizing immunity. The manuscript does not report additional discriminating virological measures (early timepoints, URT shedding, molecular assays) that would reveal whether Pam₂Cys i.n simply accelerates clearance or prevents infection. As a result, the efficacy claims based on day-7 lung PFU could partly reflect non-specific innate augmentation rather than Spike-specific immunity. This directly affects the reliability of conclusions about the vaccine construct’s mechanism and translational value.\n\"This suggests that activation of TLR2 in the nasal and lung environment can induce antigen-independent innate immunity, even weeks after i.n delivery of Pam₂Cys.\" \nThe authors explicitly acknowledge an antigen-independent mechanism that persists “even weeks” after intranasal dosing, which is temporally aligned with their challenge timeline (“three weeks post final vaccination”). This admission makes it critical to quantify the incremental benefit of adding Spike over adjuvant-only dosing under conditions where innate effects have plausibly decayed, or to use immunological interventions that isolate adaptive contributions. The paper does not, for example, include a Spike-without-adjuvant arm, nor does it test protection at later timepoints when trained innate effects may differ. Because the study’s novelty is a subunit vaccine formulation (Spike + Pam₂Cys), failing to separate adjuvant-only from antigen-driven effects undermines interpretability of the main claim. This is a major issue for causal conclusions, not a minor reporting omission.\n\"K18-hACE2 mice (n=5) were immunized with Pam2Cys alone, or Pam2Cys Spike, s.c or i.n three times, two weeks apart. ... (f) lung viral load (PFU) at day 7 p.i.\" \nThe figure caption confirms that (i) Pam₂Cys-alone i.n is a primary control arm, (ii) group sizes are small (n=5), and (iii) the key virology endpoint is terminal lung PFU at day 7. Together, these design choices make mechanistic ambiguity more consequential: with small n and a late single timepoint, strong innate-priming effects can masquerade as “sterilizing” endpoints. In a setting where adjuvant-only already drives large effects, relying on day-7 lung PFU to infer vaccine-specific mechanism is particularly fragile. Standard practice would strengthen causal attribution by including earlier timepoints, URT readouts, and/or immune perturbations, especially when innate agonists are used. Therefore, the experimental evidence as presented does not fully support the paper’s mechanistic interpretation.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|58|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb58", "comment": "The claim that the vaccine can \"minimise viral spread\" is unsupported because the study did not measure viral load in the upper respiratory tract (e.g., nasal turbinates or nasal wash), which is the primary site for transmission.\n\n\"Enhancing immunity in the respiratory tract, via mucosal vaccination, may provide protection against infection and minimise viral spread.\" (Abstract)\nThe authors suggest the vaccine can minimize viral spread. Transmission of SARS-CoV-2 primarily occurs via the upper respiratory tract (URT). Therefore, demonstrating a reduction in URT viral load is essential to support this claim.\n\"Future studies will require an assessment of the durability of protective responses achievable with this vaccination approach, including in the URT such as the nasal mucosa and trachea\" (Discussion)\nThe authors admit in the discussion that they have not yet assessed protection in the URT. This contradicts the implication in the abstract that the vaccine minimizes viral spread.\n\"Mucosal immunity and SARS-CoV-2 transmission\" [3]\nLiterature emphasizes that protection in the lungs (lower respiratory tract) does not guarantee protection in the URT, and URT viral load is the key determinant of transmission potential. Without URT data, the claim of minimizing spread is speculative.\n\nReferences:\n[3] Russell, M. W., et al. (2020). Mucosal immunity in COVID-19: A neglected but critical aspect of SARS-CoV-2 infection. Frontiers in Immunology, 11, 611337. https://www.frontiersin.org/articles/10.3389/fimmu.2020.611337/full", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|58|Gemini|5", "source": "prb", "split": "test", "paper_id": "prb58", "comment": "The paper highlights a Th17-biased CD4+ T-cell response in the lungs but fails to adequately address or test the potential safety risks associated with Th17-mediated immunopathology, which is a known concern in respiratory viral vaccines.\n\n\"Mucosally immunized mice had a substantial population of Spike-specific CD4+ T-cells locally in the lungs, predominantly secreting IL-17\" (Results)\nThe results show a dominant Th17 response. While the authors frame this as beneficial for neutrophil recruitment, Th17 responses have been linked to enhanced respiratory disease and immunopathology in other contexts.\n\"Th2 and Th17-associated immunopathology following SARS-CoV-2 breakthrough infection\" [5]\nRecent studies have indicated that Th17-associated inflammation can contribute to pathology in SARS-CoV-2 infection. The authors should have discussed this risk or performed histopathology in breakthrough/suboptimal protection scenarios to ensure the Th17 response does not exacerbate disease.\n\nReferences:\n[5] Li, C., et al. (2024). Th2 and Th17-associated immunopathology following SARS-CoV-2 breakthrough infection in Spike-vaccinated ACE2-humanized mice. Journal of Medical Virology, 96(1), e29408. https://onlinelibrary.wiley.com/doi/10.1002/jmv.29408", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|58|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb58", "comment": "In general, there is no surprise that intranasal administration of an antigen is capable of inducing IgA responses (regardless of adjuvant) and that they are neutralizing. The addition of TLR2 agonist adjuvant is a helpful addition, and the rationale for this approach is sound, and the data support the choices made here. The studies go to a lot of detail on profiling the various cells in the lung for TLR2 expression and so on, and it is not completely clear that the elaborate clustering of the flow cytometry profiles adds much to the analysis here. Given the mucosal site, adjuvant and delivery, it is disappointing that some key information was not assessed, such as specific IgG isotypes (e.g., those more likely to be associated with Th1 vs Th2 responses). Also, IgE titers and potential allergic Th2 type cytokines were not assessed.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|58|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb58", "comment": "A lot of key details were not included in this study, such as the question of whether TLR2 agonist is any more effective than any other adjuvant, such as other TLR2 agonists (e.g., targeting TLR2/6 or TLR2/1 dimers), TLR4 or TLR5 agonists which could also affect epithelial cells, or another B cell-inducing adjuvant compound. A simple mixing of the antigen and adjuvant appears adequate, though there are no additional studies to assess the impact of the specific formulation, excipients, and delivery. Moreover, while this combination is effective in inducing a good IgA response, there is much more exploration in store to assess the persistence of the response, any effect of the adjuvant on affinity maturation, and so on, though clearly these are beyond the scope of this study. But in general the impact of this study is limited by the lack of comparison to alternative approaches.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|58|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb58", "comment": "Interestingly, some of the data suggest a minor effect of intranasal TLR2 agonist even without the virus antigen, and this is perhaps even more interesting in light of the effect on infiltrating cells in the K18-hACE2 mouse infections, which may indicate some separate impact of innate immune activation on innate resistance to infection, and this is of potential interest on its own. It might be worth adding a reference to this effect in the abstract.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|58|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb58", "comment": "This paper will be of interest to those interested in seeing strategies to address ongoing and new infectious disease challenges (especially COVID) and with a few revisions it would be quite suitable for publication. The data presentation is adequate, though some of the figures are a bit busy and include data that adds relatively little to the understanding of the results. Minor revisions might include a more extended discussion of the effect of the TLR2 agonist alone, and a mention in the abstract. Also some mention of the IgG isotype and possible Th1/Th2 cytokine profiles should be included even if the data isn’t available.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|58|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb58", "comment": "A non-adjuvanted spike vaccine would be beneficial to judge on the adjuvant effect by Pam2Cys. From the data, it is very obvious that Pam2Cys plays a substantial role in inducing inflammation at the mucosal surface and even provide non-antigen-specific protection, but if this also beneficial for providing long-lasting memory responses is not clear. It would be therefore also necessary to study protection at later time points after the immunization where no unspecific effects of the adjuvant will be present anymore. Overall, the immunization schedule with 3 applications within 6 weeks and an observation period of 3 weeks post boost are rather short.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|58|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb58", "comment": "The work on the BM-chimera is really time-intensive and laborious, but the results presented here offers only limited insights in the mechanisms and the real contributions of different TLR-2 expressing cell populations. First, there are only this two selected time points (early and late) and second a non-vaccinated or even better a non-adjuvanted control is missing. A non-vaccinated control would be needed to confirm no general differences in the homeostasis of the different CD45+ populations by the missing TLR-2 signal on either the CD45+ or the epithelial compartment. Furthermore, this results are highly descriptive without direct information on the contribution to later observed immune responses. Concretely, is the early influx of neutrophils driven by TLR-2 signaling important for the IgG or IgA or CD4 T-cell response later on? To really generate mechanistic links would be very hard, but at least a kind of kinetic following the early events of cell migration and cytokine expression patterns would be nice to see.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|58|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb58", "comment": "As mentioned in the summary, it would be highly informative to study the non-specific protection of Pam2Cys alone and also to somehow establish correlates of protection for the vaccine. Since the neutralizing antibody response is so high in both vaccine groups that sterile immunity can be reached, it would be nice to see if the IgA response would be beneficial for neutralization at the mucosal surface, e.g. by neutralization assay with BAL samples against VOCs?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|58|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb58", "comment": "It is interesting to see that the T-cell response is dominated by Th17 CD4 T-cells and almost no TH1 CD4 or CD8 T-cells are induced. I think, it was expected from the previous TB study, but it would be interesting to see how these responses could contribute to the protection against SARS-CoV-2. This could be at least discusses later on.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|58|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb58", "comment": "Although I understand the value of unbiased TSNE-analyses of flow data, here it does not seem to be the best way to present the efficacy of bone marrow reconstitution (Fig. 3+4). From the plots in 3b and 4b, it is not obvious to which content the reconstitution was established and which cells mainly express TLR-2. For that, one have to look in the complicated cluster figures in the supplement. It would be nice to show the TLR-2 expression on selected populations (similar to sup.4 or 6), and estimate the percentage of TLR2+ and TLR2- cells, e.g. CD4+ TLR2+/- or DC TLR2+/- . Only from that, one could judge on the efficient depletion of CD45+ cells by irradiation and exclude residual TLR2+ cells in WT-KO mice.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|58|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb58", "comment": "The differences between the cell migration pattern in lung and BAL described for the BM-chimera are very interesting, but there is not much written or discussed about the potential reasons (e.g. different kinetics)", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|58|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb58", "comment": "However, a central criticism of this manuscript is that it is a composite of fundamental issues of TLR2 agonist Pam2Cys mediated activation and recruitment of cells to the respiratory tract, what cells are involved in signalling and what events follow ligand recognition, in both the antigen specific and antigen non-specific compartments. The studies here are well designed and well characterized.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|58|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb58", "comment": "But the primary premise of the paper is that this vaccine system will ultimately be useful for protection from SARS-CoV2. It seems that this is an add-on feature of the study to make it more timely. IL17 is the major lung cytokine produced and this cytokine as well as many of the cells that are recruited are well known to primarily protect against bacterial and fungal infections. This cytokine can also lead to lung damage and has a significant risk for proinflammatory responses in humans. Thus, the likelihood of this SARS vaccine strategy seem low.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|58|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb58", "comment": "The authors observed protection from SARS in an B6 animal model,but these data are not compelling. First, the authors use a an older transgenic model for ACE-2 expression that does not recapitulate normal expression of this SARS receptor in humans. Second, because this transgenic model is in B6 mice, and the TLR2 bone marrow chimera is developed and explored in BALB/c mice, it is difficult to extrapolate the first half of the paper with the second half. These two strains are dramatically different in T cell phenotype. So the events discovered in one strain cannot be expected to be replicated in another.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|58|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb58", "comment": "Also, and most fundamentally, the events following TLR2 engagement and robust IL17 responses are infiltration of cells that may be useful for bacterial infections but unlikely to be optimal for an viral infection.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|58|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb58", "comment": "The T cell phenotype is not fully explored and there is inadequate treatment of cells producing multiple cytokines.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|58|Human_3|7", "source": "prb", "split": "test", "paper_id": "prb58", "comment": "The sources of IL-17 are only discussed in the context of T cells -the authors should determine sources of IL-17 by methods such as direct ex vivo staining.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|59|Claude|1", "source": "prb", "split": "test", "paper_id": "prb59", "comment": "The paper proposes a \"health-oriented\" air pollution control strategy based on in vitro oxidative stress (EC₁.₅) and cytotoxicity (IC₂₀) potency values, assuming these metrics are proportional to actual human health outcomes. However, no epidemiological validation linking these specific in vitro assay endpoints to population health outcomes (such as mortality or morbidity) is provided or cited. This creates a fundamental validity concern since the paper's policy recommendations rest on unverified assumptions about the relationship between cellular-level toxicity and real-world health impacts.\n\n\"PM₂.₅-induced toxic potencies were integrated to estimate the health-relevant risk index for exposure to industrial-emitted PM₂.₅, including estimation of the PM₂.₅-induced OS and CT potency-adjusted exposure risks (TPAE_OS and TPAE_CT).\"\nThe paper introduces \"toxic potency-adjusted exposure\" as a health-relevant metric without demonstrating that these in vitro measurements actually correlate with population health outcomes. The term \"health-relevant\" implies a validated relationship with human health, but the paper relies solely on in vitro cellular assays (ROS generation and MTT assay in A549 cells) rather than epidemiological evidence linking these specific metrics to mortality or morbidity rates.\n\"Compared with the current mass-based control strategy (prioritizing implementation of ultralow emission standards in the power sector), the proposed health-oriented control strategy (priority control of the ISI sector) could generate 5.4 times higher reduction in population-weighted toxic potency-adjusted PM₂.₅ exposure among polluting industries in China.\"\nThe claim of \"5.4 times higher reduction\" in health risk is derived from multiplying PM₂.₅ concentrations by in vitro toxic potency values without validating that this product correlates with actual health outcomes. While epidemiological studies have examined source-specific PM₂.₅ health effects, the specific EC₁.₅ and IC₂₀ metrics used here have not been validated against population-level health data.\n\n* Quote from Zhang et al. (2023): \"The existing dose–response relations were generally developed based on the assumption of equal contribution to toxicity from various sources. However, the sources of PM2.5 may significantly influence health effects... The relative mortality risks of lung cancer and circulatory diseases were closely correlated with the primary emissions from industrial and residential combustion sources.\" [[1]](#citation-1)\nThis ecological study provides epidemiological evidence that source-specific PM₂.₅ may have different health effects, but uses mortality data and source apportionment—not in vitro toxicity assays—to establish health correlations. The paper under review does not demonstrate that their specific cellular ROS/cytotoxicity endpoints correspond to the epidemiologically-observed source-specific health effects.\n\n* Quote from Bates et al. (2019): \"Select OP measurements have significant associations with certain cardiorespiratory endpoints, such as asthma, congestive heart disease, and lung cancer... multiple studies have found that exposure to OP measured using the dithiothreitol and glutathione assays drives higher risk ratios for certain cardiorespiratory outcomes than PM2.5 mass\" [[2]](#citation-2)\nWhile oxidative potential has shown some epidemiological associations, this involves different assays (DTT and glutathione) than the DCFH-DA cellular ROS assay used in the reviewed paper. The paper under review does not cite epidemiological validation for its specific assay endpoints, nor does it demonstrate that EC₁.₅ values from A549 cells predict population health outcomes.\n\nReferences:\n[1] Zhang, X. et al. (2023). Ecological Study on Global Health Effects due to Source-Specific Ambient Fine Particulate Matter Exposure. *Environmental Science & Technology* 57(3), 1278-1291. https://pubs.acs.org/doi/10.1021/acs.est.2c06752\n[2] Bates, J. T. et al. (2019). Review of Acellular Assays of Ambient Particulate Matter Oxidative Potential: Methods and Relationships with Composition, Sources, and Health Effects. *Environmental Science & Technology* 53(8), 4003-4019. https://pubs.acs.org/doi/10.1021/acs.est.8b03430", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|59|Claude|2", "source": "prb", "split": "test", "paper_id": "prb59", "comment": "The study uses methanol-water sonication extraction to prepare PM₂.₅ samples for toxicity testing, but this methodology can significantly alter the chemical composition and measured toxicity of samples compared to ambient PM₂.₅. This extraction-method dependence, documented in the literature and even in a paper cited by the authors (Roper et al. 2019), raises concerns about whether the observed toxicity differences between industrial sectors reflect true differences in PM₂.₅ composition or artifacts of the extraction procedure interacting differently with sector-specific PM₂.₅.\n\n\"The PM₂.₅ filter samples were sonicated in methanol and ultra-purified water, and the obtained PM₂.₅ extracts were then dried under purified nitrogen.\"\nThe paper describes their extraction method but does not discuss how this choice may affect their results or compare their method to alternatives. Given that different industrial PM₂.₅ sources have substantially different chemical compositions (e.g., ISI PM₂.₅ has much higher metal content), the extraction method may recover different fractions of toxic constituents from each source type, potentially biasing the inter-sector comparisons.\n\n* Quote from Roper et al. (2019), cited as reference 41 in the paper: \"Significant differences were observed between extraction methods for concentrations of elements and polycyclic aromatic hydrocarbons (PAHs) of the PM2.5 tested following its preparation for biological response studies... The impact of these chemical differences on sensitive endpoints of zebrafish development was investigated. Significant differences in the percent incidence and timing of mortality were associated with PM2.5 extraction method.\" [[3]](#citation-3)\nThis paper, which the authors cite, explicitly demonstrates that extraction method significantly affects both chemical recovery and measured toxicity of PM₂.₅ samples. Notably, the study found that water and methanol extraction methods showed substantially different element recovery profiles compared to organic solvent extractions. Since ISI PM₂.₅ is metal-rich while power/cement PM₂.₅ has different compositions, the methanol-water extraction may preferentially recover metal species, potentially amplifying the apparent toxicity difference of ISI PM₂.₅.\n\n* Quote from Roper et al. (2019): \"For total elements detected in the PM2.5 extracts... the order of extraction method yield from highest to lowest concentration was: water (5.90 ± 0.023), methanol (4.94 ± 0.020), DCM (1.41 ± 0.016)... The chemical profiles resulting from the different extraction methods in this study all had an elevated contribution of hydroxy-PAHs compared to the Ambient SOP Sample.\" [[3]](#citation-3)\nThe literature shows that extraction solvent choice dramatically affects element recovery (up to 18-fold differences between methods) and alters PAH profiles. Since the paper under review found that toxic metals contributed approximately 84% of the OS potency in ISI PM₂.₅, the extraction method's efficiency in recovering metals is critical. The authors do not discuss how their chosen method may interact with the distinct chemical profiles of different industrial sources.\n\nReferences:\n[3] Roper, C. et al. (2019). PM2.5 Filter Extraction Methods: Implications for Chemical and Toxicological Analyses. *Environmental Science & Technology* 53(1), 434-442. https://pmc.ncbi.nlm.nih.gov/articles/PMC6652177/", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|59|Claude|3", "source": "prb", "split": "test", "paper_id": "prb59", "comment": "The study assigns identical toxic equivalent values for cement industry PM₂.₅ across all Chinese provinces (OS: 1.07 ± 0.47; CT: 1.37 ± 0.69), despite acknowledging that air pollution control technologies and production processes vary significantly among cement plants. This uniform application assumes homogeneity in cement PM₂.₅ toxicity regardless of local differences in kiln technology, fuel sources, raw materials, or emission control devices, potentially introducing systematic bias into the spatial analysis of toxic potency-adjusted exposure.\n\n* Quote from Supplementary Table 7: All provinces show identical cement industry OS values of \"1.07 ± 0.47\" and CT values of \"1.37 ± 0.69\" (e.g., Beijing: OS 1.07 ± 0.47, CT 1.37 ± 0.69; Shanghai: OS 1.07 ± 0.47, CT 1.37 ± 0.69; Xinjiang: OS 1.07 ± 0.47, CT 1.37 ± 0.69).\nThe exact same toxic potency values applied uniformly across all 31 provinces indicates that the provincial-level toxic potency-adjusted exposure calculations for cement industry contributions do not account for any regional variation in cement plant characteristics. This contrasts with the paper's own finding that different cement processes (kiln head vs. kiln tail) show different toxicity profiles, suggesting within-industry variation that should be reflected at the provincial level.\n\n* Quote from Supplementary Materials: \"The same TU values were adopted for the cement plants across different provinces owing to the similarity of the kiln and control technology applied among cement plants in mainland China.\"\nThis statement justifies uniform values based on technological similarity, but contradicts the paper's own data showing different EC₁.₅ values between kiln head (113.4 ± 53.0 µg/mL) and kiln tail (98.7 ± 39.9 µg/mL) processes. Furthermore, the paper cites literature acknowledging that \"different types of kilns, including precalciner kilns, shaft kilns, and other rotary kilns\" exist in China, and that local ULE standards vary by province. The assumption of uniform toxicity ignores this documented heterogeneity.\n\"Precalciner kiln emissions are the largest contributor to PM emissions of the cement industry, accounting for 80% of the total PM emissions in 2015. PM emissions originating from shaft kilns, other rotary kilns, and cement grinding could be neglected. Nearly 83.5% of the cement industry met the new 2015 standards by the end of 2018.\"\nThis passage acknowledges temporal evolution in control technology adoption and residual heterogeneity (16.5% not meeting standards). The implicit assumption that the ~17% of plants not meeting standards have the same PM₂.₅ toxicity as compliant plants is not supported. Additionally, the varying adoption of local ULE standards across \"six key provinces\" mentioned in the supplementary materials would likely create provincial-level toxicity differences not captured in the uniform values.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|59|GPT|1", "source": "prb", "split": "test", "paper_id": "prb59", "comment": "This paper defines toxic units (TUs) as the reciprocal of sample-level EC\\_1.5/IC\\_20 endpoints but then aggregates provincial TUs as the reciprocal of an emission-weighted average of EC\\_1.5/IC\\_20, a non-equivalent transformation that can substantially bias toxic equivalent values and therefore the sector-ranking and policy conclusions derived from toxic potency-adjusted exposure (Supplementary Note 9).\n\nToxic units (TUs), including estimation of PM_{2.5}-induced OS and CT potency values, can be estimated as follows: TUOS_{j,s} = \\frac{1}{(\\mathrm{EC}_{1.5})_{j,s}} and TUCT_{j,s} = \\frac{1}{(\\mathrm{IC}_{20})_{j,s}}, where j and s denote sample (j) and industry source (s), respectively, EC_{1.5} is the endpoint of the PM_{2.5}-induced OS potency, indicating the concentration causing a 1.5-fold increase in intracellular ROS formation relative to that in the control group, IC_{20} is the endpoint of the PM_{2.5}-induced CT potency, indicating the concentration causing 20% inhibition of the cell viability relative to that in the control group.\nThis passage unambiguously defines TU as an inverse mapping from an endpoint concentration (EC\\_1.5 or IC\\_20) to a “toxic unit.” Once TU is defined as 1/EC or 1/IC, any aggregation across processes or samples that aims to represent a mixture or a sector should be done in TU-space (i.e., by combining 1/EC values with appropriate weights). Otherwise, the aggregation no longer corresponds to the stated definition of TU and will systematically deviate whenever EC/IC varies across components. Because the paper’s central premise is “unequal toxicities,” substantial variation is expected, making this discrepancy practically important rather than a negligible algebraic detail. The rest of the analysis (toxic equivalents, TPAE, and control rankings) depends on these aggregated toxicity metrics, so any bias here propagates directly into headline results.\nThe average provincial TUs of industrial PM_{2.5} emissions can be estimated as follows: TUOS_{i,s} = \\frac{1}{\\sum (\\mathrm{EC}_{1.5})_{j,s} \\times \\mathrm{WF}_{j,s}} and TUCT_{i,s} = \\frac{1}{\\sum (\\mathrm{IC}_{20})_{j,s} \\times \\mathrm{WF}_{j,s}}, where WF is the weighing factor, estimated based on the mass fraction of PM_{2.5} emissions of each individual manufacturing process (or each individual fuel-fired unit) to the total PM_{2.5} emission amount of all manufacturing processes (or all fuel-fired units).\nThis formula computes TU as the reciprocal of a weighted *arithmetic mean* of EC\\_1.5/IC\\_20, which is generally not equal to the weighted mean of the reciprocals (the TU values) implied by the earlier TU definition. The difference can be large under heterogeneity (e.g., mixing a highly potent component with a weakly potent one), exactly the regime the paper emphasizes. Because the weighting factor WF is emission-mass-based, the natural toxicity-weighted mixture metric—consistent with a linear “per mass” potency framing—would be Σ WF·(1/EC) rather than 1/Σ WF·EC. The paper does not justify why the nonlinear reciprocal-of-mean is the correct mixture rule for toxicity units, nor does it provide a sensitivity analysis showing the ranking is invariant to this choice. As a result, the quantitative toxic equivalents and exposure-risk reductions can be artifacts of this aggregation choice rather than robust reflections of underlying toxicity measurements.\nTPAE<sub>OS</sub> and TPAE<sub>CT</sub> were estimated as TPAE<sub>OS</sub> = C<sub>i,s</sub> × OS<sub>i,s</sub> and TPAE<sub>CT</sub> = C<sub>i,s</sub> × CT<sub>i,s</sub>, respectively, where OS<sub>i,s</sub> and CT<sub>i,s</sub> are the toxic equivalent values of the PM<sub>2.5</sub>-induced OS and CT potency, respectively, originating from each industry sector (s) in each geographic unit (i).\nThis shows that the toxic equivalent values (OS\\_{i,s}, CT\\_{i,s}) are direct multiplicative factors in the paper’s population-relevant risk index (TPAE). Therefore, any bias in TU aggregation that feeds into OS/CT equivalents will proportionally bias TPAE and any reported “times higher” reductions. Because the core policy recommendation is based on relative reductions in population-weighted TPAE under alternative sector priorities, even moderate systematic distortion of OS/CT equivalents can flip or exaggerate the comparison. The formulation also implies a linear scaling of “risk” with these equivalence factors, so the exact construction of OS/CT equivalents is not a cosmetic methodological choice but a structural determinant of results. The paper provides no validation that its particular TU aggregation rule preserves ordering under realistic intra-sector variability, which undermines confidence in the downstream comparisons.\nThe toxic equivalent (TEQ) is operationally defined by the sum of the products of the concentration of each congener multiplied by its TEF value.\nThis statement describes the standard logic of toxicity-equivalency aggregation: overall mixture toxicity is represented as a *linear* sum of component contributions in the form Σ(concentration × equivalency factor), rather than by applying a nonlinear reciprocal transformation after averaging. While the paper’s pollutants and endpoints differ (industrial PM vs. dioxin congeners), the key methodological parallel is the mixture-combination principle used to build a single index from heterogeneous components. If the paper intends TUs/TEs to play an analogous “equivalency factor” role, a linear mass-weighted combination is the default and widely used approach in regulatory and risk-assessment settings. The paper’s reciprocal-of-weighted-mean construction deviates from this norm without justification, which is especially concerning because it can systematically downweight extreme toxicities. This mismatch strengthens the concern that the paper’s aggregation step is not only internally inconsistent but also out of line with established equivalency frameworks. [\\[3\\]](#ref3)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|59|GPT|2", "source": "prb", "split": "test", "paper_id": "prb59", "comment": "This paper makes strong policy claims about “health-oriented” control and “exposure risks” using toxic potency-adjusted exposure (TPAE) that is built from in vitro A549 oxidative-stress/cytotoxicity endpoints measured on extracted primary stack PM, without demonstrating that TPAE is a valid surrogate for real-world human health outcomes or that its assumed linear scaling supports sector-priority decisions.\n\nCompared with the current mass-based control strategy (prioritizing implementation of ultralow emission standards in the power sector), the proposed health-oriented control strategy (priority control of the ISI sector) could generate 5.4 times higher reduction in population-weighted toxic potency-adjusted PM<sub>2.5</sub> exposure among polluting industries in China.\nThis sentence elevates “toxic potency-adjusted PM\\_2.5 exposure” to the central outcome for comparing policies and motivates a sector-priority shift. However, “toxic potency-adjusted exposure” is not a standard epidemiologic effect metric (e.g., attributable mortality or morbidity), and the paper does not show how a given percentage reduction in TPAE maps to an expected reduction in health outcomes. Without such calibration, the “5.4 times higher reduction” is only meaningful within the authors’ constructed index, not necessarily for human health. The claim is especially consequential because it frames existing regulations as mis-prioritized and proposes an “urgently required” alternative; that level of prescription typically requires outcomes that are validated against human data or at least mechanistically linked through well-supported dose–response relationships. As written, the paper risks over-interpreting an index built from in vitro endpoints as if it were a health-impact function.\nHuman epithelial A549 cell lines were adopted to examine PM<sub>2.5</sub>-related biological effects, including PM<sub>2.5</sub>-induced oxidative stress (OS) potency and cytotoxicity (CT) potency.\nThis establishes that the toxicity signal driving the policy analysis is derived from a single in vitro cell line assay platform, rather than from in vivo or epidemiologic evidence. A549 assays are useful for mechanistic screening, but translating their dose–response endpoints to population-level exposure risk is nontrivial because real exposures involve complex deposition, clearance, metabolism, and systemic responses not represented in monoculture assays. The paper also uses solvent extraction (“sonicated in methanol and ultra-purified water”) before testing, which can change the bioavailable fraction of components relative to inhalation exposure and complicate interpretability across sources. Critically, the paper does not demonstrate that the relative ranking of source toxicities in A549 assays persists under more realistic exposure models or across multiple relevant endpoints (e.g., inflammation, cardiovascular pathways). Because TPAE is built from these endpoints, the absence of validation threatens the robustness of the downstream sector-priority recommendation.\nTPAE<sub>OS</sub> and TPAE<sub>CT</sub> were estimated as TPAE<sub>OS</sub> = C<sub>i,s</sub> × OS<sub>i,s</sub> and TPAE<sub>CT</sub> = C<sub>i,s</sub> × CT<sub>i,s</sub>, respectively, where OS<sub>i,s</sub> and CT<sub>i,s</sub> are the toxic equivalent values of the PM<sub>2.5</sub>-induced OS and CT potency, respectively, originating from each industry sector (s) in each geographic unit (i).\nThis construction implicitly assumes that “health-relevant risk” scales linearly with modeled concentration (C\\_{i,s}) and a single scalar toxic-equivalence multiplier (OS\\_{i,s} or CT\\_{i,s}) derived from in vitro endpoints. In practice, health impact assessment typically requires an exposure–response function (often nonlinear and outcome-specific) and baseline risk information; a simple product index can be informative for ranking hypotheses but is not automatically a valid risk surrogate. The paper does not provide any empirical evidence that a unit change in OS-equivalent or CT-equivalent translates into proportional changes in morbidity/mortality, nor does it evaluate whether the chosen endpoints represent the dominant pathways of PM\\_2.5 health effects. Because the policy comparisons and cost-effectiveness conclusions are made “per unit of toxic potency-adjusted mass,” any misspecification of this index can materially alter which sector appears most beneficial to control. The linear product form therefore requires external validation that is not shown in the manuscript.\nWe point out here the potential dangers of exclusive use of an in vitro screening approach in view of experience with other particles, suggesting that particles can cause a rather narrow range of effects on cells in culture which does not reflect the range of different pathogenic effects they cause in vivo.\nThis review directly cautions against using in vitro oxidative-stress-type screens as a stand-alone basis for hazard ranking across particle types, because similar cellular oxidative stress responses can correspond to very different in vivo pathologies. That warning applies to this paper’s strategy of using A549-based OS/CT potency endpoints as the core toxicity input for nationwide policy ranking. Even if the assays are executed carefully, the quote highlights that the mapping from in vitro response to in vivo disease outcomes can be weak or ambiguous without supporting toxicokinetic and in vivo evidence. The paper’s central claim is not merely mechanistic (that industrial PM differs in potency), but prescriptive (that control priorities should change to protect health), which requires stronger validation than a screening endpoint alone. The external critique therefore strengthens the concern that the paper’s “health-oriented” index may not reliably predict actual health benefits from sector-specific controls. [\\[1\\]](#ref1)\nHealth impact assessments typically use a single log-linear CR function per health outcome to estimate counts of avoided human health effects resulting from air quality improvements.\nThis statement summarizes a widely used practice in policy-relevant health impact assessment: converting exposure reductions into avoided health outcomes through concentration–response (CR) functions grounded in epidemiology. In contrast, the paper’s TPAE does not specify a CR function relating its toxicity-weighted exposure to concrete outcomes (e.g., mortality), and therefore cannot be directly interpreted as “health effects” avoided. Because the paper claims “cost-effective reductions in particulate exposure risks,” readers would reasonably expect an outcome-linked risk model or at least a demonstration that TPAE is predictive of outcome changes. The absence of such linkage means that the comparative effectiveness ratios (e.g., “5.4 times higher reduction”) may not correspond to proportional differences in avoided disease burden. This discrepancy undermines the robustness of the conclusions for real-world health-oriented regulation, even if TPAE is a useful exploratory index for hypothesis generation. [\\[5\\]](#ref5)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|59|GPT|3", "source": "prb", "split": "test", "paper_id": "prb59", "comment": "This paper’s sector-contribution estimates and “health-oriented” control prioritization are potentially biased because they explicitly omit source-specific secondary aerosol formation and fugitive emissions from key industrial processes and, in attribution scenarios, remove only primary PM<sub>2.5</sub> emissions; this can materially change both exposure burdens and the ranking of which sector should be prioritized.\n\nSource-specific secondary and fugitive aerosols emission from manufacturing iron/steel and cement processes were not considered, which could result in underestimation of the adverse impacts associated with exposure to specific source-emitted aerosols.\nThis admission directly affects the paper’s central comparison of sector priorities because excluding secondary and fugitive components changes both the magnitude and spatial distribution of exposure attributable to each sector. Industrial sectors differ substantially in precursor emissions (e.g., SO\\_2, NO\\_x, VOCs, NH\\_3 interactions) and in fugitive dust contributions; omitting these components can therefore alter relative burdens, not just absolute totals. The claim that ISI should be prioritized over power based on toxic potency-adjusted exposure reductions depends on accurate sector-attributable concentrations, which are compromised if key aerosol pathways are missing. Importantly, the limitation is not a marginal refinement: secondary formation often dominates ambient PM\\_2.5 composition in many regions, and industrial precursors are major drivers of that formation. Without quantifying the direction and magnitude of this omission, the policy ranking is not reliably supported.\nEmission inventories excluding primary PM<sub>2.5</sub> emissions from power, cement, and ISI sectors, as obtained with the baseline scenarios, were used to simulate the NoELE, NoCI, and NoISI scenarios, respectively.\nThis sentence indicates that sector attribution is performed by “zeroing out” only primary PM\\_2.5 emissions, not the gaseous precursors that form secondary PM\\_2.5 attributable to the same sectors. As a result, the computed “ambient PM\\_2.5 concentration attributable to the power, cement, and ISI sectors” will systematically miss secondary contributions from those sectors and can misrepresent sector responsibility for population exposure. This is particularly problematic for comparing sectors because power and heavy industry have distinct precursor profiles and stack heights, affecting downwind secondary production differently. The paper’s toxicity-weighting then multiplies these potentially incomplete concentrations by toxicity equivalents, compounding errors in both concentration and toxicity dimensions. Therefore, the attribution approach is not aligned with the paper’s stated goal of assessing health-relevant impacts of industrial emissions in the atmosphere.\nAs for the population-weighted TPAE, we limited our uncertainty analysis to the emission inventory owing to the near-linear response of the ambient PM_{2.5} concentration to the primary PM_{2.5} emission.\nThis sentence reflects an analytical framing in which primary PM\\_2.5 emissions are treated as the dominant driver of the modeled concentration responses relevant for TPAE. However, secondary aerosol formation is explicitly acknowledged elsewhere as omitted, so assuming a near-linear response to primary PM\\_2.5 is not a safe basis for concluding that ignoring these pathways does not affect rankings. Even within primary PM\\_2.5, the relationship between emissions and population-weighted concentration can be nonlinear due to meteorology, plume rise, and chemistry affecting particle dynamics, which would be handled by the chemical transport model rather than assumed. By tying both attribution and uncertainty choices to primary PM\\_2.5 only, the paper structurally limits its ability to support conclusions about comprehensive industrial PM\\_2.5 exposure burdens. This weakens the validity of using the resulting TPAE reductions as the decisive basis for sector-priority policy.\nSecondary fine particles - Fine particles that form in complicated reactions in the atmosphere of chemicals, such as sulfur dioxides and nitrogen oxides, that are emitted from power plants, industries, and automobiles.\nThis definition highlights that secondary fine particles arise from atmospheric reactions of emitted precursor gases and that power plants and industries are explicitly among the sources of those precursors. Therefore, a sector-attribution framework that removes only primary PM\\_2.5 emissions will, by construction, omit an important class of PM\\_2.5 that is causally attributable to the same sectors through precursor emissions. Because the paper’s objective is “health-oriented air pollution control,” omitting secondary PM\\_2.5 undermines the completeness of exposure assessment and may skew which sectors appear most beneficial to control. The quote reinforces that secondary PM\\_2.5 is not an exotic niche component but a recognized and policy-relevant pathway for how industrial activities create fine-particle exposures. Consequently, the paper’s conclusions about optimal sector prioritization are not adequately supported without incorporating (or bounding) secondary PM\\_2.5 contributions. [\\[2\\]](#ref2)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|59|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb59", "comment": "The study incorrectly applies the toxic potency measured from primary PM2.5 emissions to the total ambient PM2.5 concentration attributable to each industrial sector, which includes a significant fraction of secondary inorganic aerosols (sulfate and nitrate) that have much lower toxicity.\n\n\"TPAE_OS = C_i,s × OS_i,s\"\nThis equation multiplies the total ambient concentration attributable to a sector ($C_{i,s}$) by the oxidative stress potency of the primary emissions ($OS_{i,s}$). This assumes that all PM2.5 originating from a sector (including secondary aerosols formed in the atmosphere) has the same toxicity as the primary particles emitted from the stack.\n\"The differences in the simulated concentrations between the baseline scenario and the NoELE, NoCI, and NoISI scenarios were employed to estimate the ambient PM2.5 concentration attributable to the power, cement, and ISI sectors, respectively.\"\nThe \"zero-out\" method in WRF-CMAQ captures the total contribution of a sector, which includes both primary PM and secondary PM formed from precursor emissions (SO2, NOx). For industrial sectors like power and iron/steel, secondary sulfates and nitrates often constitute a large portion of their total ambient PM2.5 contribution.\n\"while many of the major PM components, including inorganic sulfate and nitrate, are commonly considered innocuous species\"\nThe authors themselves acknowledge in the Introduction that secondary inorganic components are less toxic. However, their methodology treats these components as having the same high toxicity as the metal-rich primary particles from the Iron and Steel Industry (ISI).\n\"secondary inorganic components, crustal material and secondary biogenic organic aerosols control the mass concentration of particulate matter... [but] anthropogenic secondary organic aerosols and metals from non-exhaust traffic emissions and biomass burning are the main drivers of the oxidative potential\" [1]\nLiterature shows that while secondary inorganics drive mass, they do not drive oxidative potential. By applying the high toxicity of primary ISI particles (rich in metals) to the secondary sulfate/nitrate fraction, the study vastly overestimates the health risk of ISI emissions and the benefits of their control.\n\"Extensive animal and human toxicology data show no significant effects for particles consisting only of sulfate and nitrate compounds at levels in excess of ambient concentrations.\" [4]\nThis further supports that sulfate and nitrate, which are major components of the ambient PM2.5 attributed to industrial sources in the model, have negligible toxicity compared to the metal-rich primary particles. Treating them as equally toxic to primary ISI emissions is a critical methodological flaw.\n\nReferences:\n[1] Daellenbach, K. R., et al. (2020). Sources of particulate-matter air pollution and its oxidative potential in Europe. *Nature* 587, 414-419. (https://www.nature.com/articles/s41586-020-2902-8)\n[4] Reiss, R., et al. (2007). Evidence of health impacts of sulfate-and nitrate-containing particles in ambient air. *Inhalation Toxicology* 19(5), 419-449. (https://pubmed.ncbi.nlm.nih.gov/17365047/)", "reviewer_type": "ai", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|59|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb59", "comment": "The paper frames the \"current strategy\" as prioritizing power plants and compares the proposed strategy against a scenario where power plants have no ultralow emission (ULE) standards, despite the fact that ULE retrofitting in the power sector was largely completed before the study's base year.\n\n\"Compared with the current mass-based control strategy (prioritizing implementation of ultralow emission standards in the power sector), the proposed health-oriented control strategy... could generate 5.4 times higher reduction\"\nThis statement implies that the \"current strategy\" is an active choice between Power ULE and ISI ULE. However, Power ULE is largely a completed action, not a competing alternative for future implementation.\n\"By the end of 2017, all CFPP units had already satisfied the emission standards (GB 13223-2011)⁴, while 72.3% of all CFPPs in mainland China had met the ULE standards\"\nThe Supplementary Material confirms that the \"ELE_noULE\" scenario represents a counterfactual past (pre-2017 status), not the current policy landscape. Comparing the potential benefits of a future action (ISI ULE) against the benefits of a past action (Power ULE) is valid for retrospective analysis but misleading when framed as a guide for immediate future strategy selection.\n\"The differences between the baseline and ELE_noULE scenarios constitute the influence of the ULE standard for PM control implemented at power plants since 2015 in China.\"\nThe authors explicitly state that this scenario represents the influence of past implementation. The abstract should clearly reflect that the comparison is between a proposed future strategy and a historically implemented one, rather than implying a trade-off between two current options.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|59|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb59", "comment": "The use of methanol and water extraction for toxicity assays likely underestimates the toxicity of metal-rich particles from the Iron and Steel Industry, as many relevant metal species (e.g., iron oxides) may be insoluble in these solvents.\n\n\"The PM2.5 filter samples were sonicated in methanol and ultra-purified water, and the obtained PM2.5 extracts were then dried under purified nitrogen.\"\nThis extraction method recovers only soluble components. While methanol extracts organics, water extracts soluble ions. Many transition metals found in industrial emissions, particularly from high-temperature processes like steelmaking, exist as insoluble oxides or bound in aluminosilicate matrices.\n\"Fe dominated the mass concentrations, with relative concentrations ranging from 62.6 − 98.3%... in the selected metals within in PM2.5 emitted from the ISI\"\nSince iron is the dominant metal in ISI emissions and is often present as insoluble oxides (e.g., hematite, magnetite), a significant portion of the metal mass—and potentially its surface-mediated toxicity—may be excluded from the liquid extract used for cell exposure. This could lead to an underestimation of the absolute toxicity of ISI particles, although it does not necessarily invalidate the relative ranking if ISI is still found to be the most toxic.\n\"Some results do suggest a degree of differential toxicity, namely more consistent associations with traffic-related PM emissions, fine and ultrafine particles.\" [2]\nLiterature emphasizes that particle size and surface area (often associated with insoluble cores) are determinants of toxicity. By using only extracts, the study neglects the physical effects of particles and surface-bound reactivity of insoluble fractions.\n\"Total iron solubility fractions measured in the dark after 12 h ranged between 2.9 and 74.1% of the initial iron content for the combustion-derived particles... in acidic media\" [3]\nIron solubility is highly dependent on pH and is generally low in neutral water. Since the study used water/methanol extraction (likely neutral pH), the dissolution of iron oxides would be minimal compared to acidic conditions (mimicking lysosomal fluid) or total digestion. This confirms that the extraction method likely missed a large fraction of the iron.\n\"The surface of the particles... generates ROS... transition metals on the surface of particles... are responsible for the formation of hydroxyl radicals\" [5]\nThe surface reactivity of insoluble particles is a key mechanism of toxicity. By removing the solid particles and testing only the extract, the study ignores this crucial pathway, potentially underestimating the toxicity of the metal-rich ISI particles.\n\nReferences:\n[2] Kelly, F. J., & Fussell, J. C. (2012). Size, source and chemical composition as determinants of toxicity attributable to ambient particulate matter. *Atmospheric Environment* 60, 504-526. (https://doi.org/10.1016/j.atmosenv.2012.06.039)\n[3] Chen, H., et al. (2012). Solubility of iron from combustion source particles in acidic media linked to iron speciation. *Environmental Science & Technology* 46(20), 11171-11178. (https://pubs.acs.org/doi/abs/10.1021/es302558m)\n[5] Valavanidis, A., et al. (2008). Airborne particulate matter and human health: toxicological assessment and importance of size and composition of particles for oxidative damage and carcinogenic mechanisms. *Journal of Environmental Science and Health, Part C* 26(4), 339-362. (https://doi.org/10.1080/10590500802494538)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|59|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb59", "comment": "Lines 70-71: Why did the authors select the iron and steel industry (ISI), power industry, and cement industry as the targets of industrial sectors in this study? What contribution do these industrial sectors make to ambient air pollution or PM2.5 levels?", "reviewer_type": "human", "label": "error", "error_type": "Neglect", "label_origin": "expert+llm-filter"}
{"id": "prb|59|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb59", "comment": "Lines 172-175: The results indicate that the PM2.5-induced oxidative stress (OS) potency could mainly be attributed to PM2.5-bound toxic metals. Calculating PM2.5-induced OS potency for selected metals and PAHs is based on reference models, which can be found in the study by Jin et al. (2019). That study provided EC1.5 and REP for valence metals. However, ICP-MS does not analyze metal valence. The authors should clarify the OS potency concentrations from metals and make assumptions if necessary. In addition, the calculations of OP are not transparent the authors only presented references.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|59|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb59", "comment": "Have any prior experimental studies investigated the toxic effects of industrial PM2.5? It’s necessary to compare the findings with earlier research.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|59|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb59", "comment": "Numerous studies in environmental epidemiology have investigated the impact of PM2.5 compositions on public health. It is essential for authors to analyze and contrast the variations between their study and previous epidemiology research in this field.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|59|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb59", "comment": "Line 62-63 “while many of the major PM components, including inorganic sulfate and nitrate, are commonly considered innocuous species17.”, the author should double check the sentence. The reference is out of date and there are many epidemiology studies found the toxic of inorganic sulfate. Modifying the acidity and alkalinity levels could potentially impact the toxicity of metals present in PM2.5.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|59|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb59", "comment": "Line 140-142 “Here, the targeted chemicals are focused on metals and PAHs, which are commonly regarded as key toxic components associated with the biological effects of PM2.5.”, please explain why black carbon or elemental carbon is not a targeted chemicals in this studies?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|59|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb59", "comment": "It is recommended to include the proportion of certain key constituents, such as inorganic sulfate and nitrate, in Supplementary Table 4.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|59|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb59", "comment": "What methodology did the author employ to compute the information presented in Supplementary Figure 7a?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|59|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb59", "comment": "While I agree with the authors that the toxicity of particulate matter varies with source, the sampling collection and handling methods used in this work are not appropriate for the toxicity tests they perform. The sampling methods documented in the supplementary materials fails to collect the condensible particulate matter, which is where much of the most toxic components result in the ambient air. What is required is a dilution sampling system to allow the reaction and condensation closer to what happens once the particles, vapors, and gases are released into the atmosphere. One appropriate method is described here: England GC, Watson JG, Chow JC, Zielinska B, Chang MC, Loos KR, Hidy GM. Dilution-based emissions sampling from stationary sources: Part 1--Compact sampler methodology and performance. J Air Waste Manag Assoc. 2007 Jan;57(1):65-78. doi: 10.1080/10473289.2007.10465291. PMID: 17269232.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|59|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb59", "comment": "A second problem with the methods is that no mention is made of post collection sample handing to protect the sample acidity from neutralization. A proper storage would place samples collected into containers with citric acid coated material to prevent neutralization of acids, such as sulfuric acid, until use in the toxicological tests, also under ammonia free conditions. This is especially important in fossil fuel combustion particulate matter, high in acidic sulfur, which is known to activate transition metals by making them bioavailable (e.g., see: Fang, T.; Guo, H.; Zeng, L.; Verma, V.; Nenes, A.; Weber, R.J. Highly Acidic Ambient Particles, Soluble Metals, and Oxidative Potential: A Link between Sulfate and Aerosol Toxicity. Environmental Science & Technology 2017, 51, 2611-2620, doi:10.1021/acs.est.6b06151).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|59|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb59", "comment": "The role of sulfates is dismissed as relatively non-toxic by the authors in their discussion, but this is not a full consideration of its role. In isolation, it is true that its toxicity is low, but in combination with metals (as always occurs in the real world) acidic sulfur has an important role, as indicated by the epidemiological evidence, which the authors fail to acknowledge. For example, see: Weichenthal S, Lavigne E, raub A, Umbrio D, You H, Pollitt K, Shin T, Kulka R, Stieb DM, Korsiaik J, Jessiman B, JBrook JR, Hatzopoulou M, Evans G, Burnett RT, Association of Sulfur, Transition Metals, and the Oxidative Potential of Outdoor PM2.5 with Acute Cardiovascular Events: A Case-Crossover Study of Canadian Adults. Environmental Health Perspectives. Environ Health Perspect 129(10). (2021). doi: 30 10.1289/EHP9449.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Claude|1", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "The paper assumes that temperature-related deaths and COVID-19 deaths are independent and simply adds them together to estimate compound mortality impacts. However, extensive literature demonstrates that vulnerable populations for heat/cold mortality and COVID-19 mortality substantially overlap (elderly, those with chronic conditions), which violates this independence assumption and may lead to either double-counting or underestimation of compound effects.\n\n\"By adding temperature-related deaths (with COVID-19 deaths removed prior to calculation) and COVID-19 deaths together to estimate the compound mortality impact, we have assumed that they are independent of each other.\"\nThe paper explicitly acknowledges this assumption but does not adequately address its implications for the validity of the compound mortality estimates. Simply removing COVID-19 deaths from the mortality data before fitting the temperature-mortality model does not account for potential effect modification, where COVID-19 may have amplified temperature-mortality relationships through shared vulnerabilities, behavioral changes, or healthcare system strain. The approach of treating these as additive effects may misrepresent the true compound risk.\n\"Because of the common risk factors for temperature-related and COVID-19 mortality, disentangling their effects on health and attributing mortality to a single cause is challenging.\"\nThe paper acknowledges this challenge in the discussion but proceeds with the additive assumption nonetheless. This creates a fundamental tension between the methodology used and what the authors recognize as a limitation. Recent studies using interaction models have found that heat-related mortality was significantly elevated during COVID-19 (RR=1.55) compared to pre-pandemic periods (RR=1.07), suggesting the relationship is not simply additive but involves effect modification.\n\"Heat–pathogen interactions likely influence COVID-19 mortality, as vulnerable populations overlap: the elderly, chronically ill, and those requiring care\" [[1]](#citation-list)\nThis recent study (Ali et al., 2025) in Nature Scientific Reports explicitly quantified the interaction between heat and COVID-19 on mortality using a time-stratified case-crossover design with interaction terms. They found a significant synergistic effect where the risk of heat-related mortality increased with COVID-19 intensity (RR reaching 3.57 during high COVID-19 incidence). This methodological approach directly models the interaction rather than assuming independence, representing a more appropriate analytical framework for compound hazard assessment.\n\nReferences:\n[1] Ali, E.A., et al. (2025). The overlapping impacts of heat and COVID-19 on mortality in Flanders, Belgium: a time-stratified case-crossover analysis. *Scientific Reports* (Nature). https://www.nature.com/articles/s41598-025-25481-8", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Claude|2", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "The study derives temperature-mortality associations using 41 years of data (1981-2022) with COVID-19 deaths simply removed, then applies these relationships to estimate temperature-related mortality during 2020-2022. This approach assumes the temperature-mortality relationship remained unchanged during the pandemic, despite substantial changes in population behavior, healthcare access, and social conditions that may have altered vulnerability to temperature extremes.\n\n\"Since the 2020–2022 mortality data include COVID-19 deaths, which we want to separate from temperature-related deaths in this study, we remove deaths with COVID-19 on the death certificate from the all-cause mortality data. We then derive the non-linear association between the temperature and mortality time series using quasi-Poisson regression with DLNMs, adapting the methods from previous studies.\"\nThis methodology treats the pandemic period as equivalent to pre-pandemic years in terms of the temperature-mortality relationship, which is problematic. Pandemic conditions included lockdowns that limited access to cooling centers, social isolation that reduced checks on vulnerable individuals, healthcare system strain, and behavioral changes. These factors may have modified how temperature affected mortality during 2020-2022, meaning relationships derived primarily from pre-pandemic data may not accurately capture pandemic-period dynamics.\n\"Future work is recommended to understand the confounding effect(s) of COVID-19 on temperature-related health outcomes. For example, instead of using all available observed temperature and mortality data (1981–2022 data, but with reported COVID-19 mortality removed) to construct the DLNMs here (see Methods), future work can derive temperature-mortality associations using only data from the COVID-19 time period. We have not done this because two years of data (in the COVID-19 period of 2020–2022) are not enough to derive constrained temperature-mortality associations with low uncertainty on the regional level.\"\nThe authors acknowledge this limitation but proceed with the analysis nonetheless. While the concern about insufficient data for pandemic-only analysis is valid, the alternative approach used may systematically bias temperature-related mortality estimates. The Carbon Brief coverage of this paper notes that the author acknowledged \"a lot of vulnerabilities to temperatures and Covid-19 are shared\" and that pandemic measures like \"closing social spaces, such as swimming pools and air-conditioned buildings, meant that many people didn't have as much of an escape from the high temperatures\" [[2]](#citation-list).\n\"heat-related mortality in 2020 was indirectly amplified by the COVID-19 pandemic, attributing this to reduced healthcare access and delayed heat adaptation strategies\" [[3]](#citation-list)\nSousa et al. (2022) found evidence that the pandemic itself altered heat-mortality relationships through multiple pathways. This supports the concern that using pre-pandemic derived relationships may not accurately characterize temperature-related mortality during the pandemic period, potentially biasing the estimates used in this study.\n\nReferences:\n[2] Carbon Brief (2024). Dual impact of extreme heat and Covid-19 had 'deadly consequences' for UK. https://www.carbonbrief.org/dual-impact-of-extreme-heat-and-covid-19-had-deadly-consequences-for-uk/\n[3] Sousa, P.M., et al. (2022). Heat-related mortality amplified during the COVID-19 pandemic. *International Journal of Biometeorology* 66:457–468. https://pubmed.ncbi.nlm.nih.gov/34729651/", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Claude|3", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "The paper uses two-sample Kolmogorov-Smirnov tests to conclude that temperature-related mortality distributions during COVID-19 years differ significantly from non-COVID years. However, the number of extreme temperature events is limited (approximately 10-22 heatwaves and 8-24 cold snaps across the periods), which may affect the statistical power and reliability of these conclusions.\n\n\"Two-sample Kolmogorov–Smirnov tests confirm that the COVID-19 event distributions are significantly different from the non-COVID-19 distributions at the 5% significance level. These results suggest that COVID-19 may have impacted temperature-related mortality during extreme weather events.\"\nThe conclusion that COVID-19 \"may have impacted\" temperature-related mortality is drawn from K-S tests applied to limited samples. From the code and figure descriptions, the comparison involves approximately 12 heatwaves in 2016-2019 versus 10 heatwaves in 2020-2022, and similar numbers for cold snaps. With such small sample sizes, the K-S test may have limited power to detect true differences or may be sensitive to individual outliers, making the statistical significance potentially unstable.\n\"although the number of extreme temperature events sampled is limited by the short study period\"\nThe paper acknowledges this limitation. However, the statistical methodology and presentation of results do not adequately reflect this uncertainty. Statistical power analyses for K-S tests indicate that detecting moderate effect sizes (δ=0.5) at 80% power requires sample sizes of approximately 52 or more per group [[4]](#citation-list). The analysis presented falls well short of this requirement, suggesting the significant p-value should be interpreted with caution and the conclusions about COVID-19 impacting temperature-mortality relationships remain tentative.\n\n* Quote (from Figure 4 caption): \"In panel a, grey markers indicate heatwaves in 2016-2019, whereas coloured markers indicate heatwaves in COVID-19 affected years: 2020 (pink), 2021 (red) and 2022 (dark red).\"\nThe figure shows scattered data points representing individual heatwave events by region. While the visual separation of the ellipses suggests different distributions, the underlying sample sizes are small. Each heatwave event contributes 10 data points (one per region), but these are not independent observations—all regions experience the same weather event simultaneously. The effective sample size for comparing event-level distributions is the number of distinct weather events, not the number of region-event combinations.\n\nReferences:\n[4] Boyerinas, B.M. (2016). Determining the Statistical Power of the Kolmogorov-Smirnov and Anderson-Darling Goodness-of-Fit Tests via Monte Carlo Simulation. CNA Analysis & Solutions. https://www.cna.org/archive/CNA_Files/pdf/dop-2016-u-014638-final.pdf", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Claude|4", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "The paper reports incorrect dates for the Heat Health Alerts issued during the July 2022 unprecedented heatwave, stating alerts were issued in July 2021 when discussing events that occurred in July 2022.\n\n\"Although the UK Met Office and UK Health Security Agency (UKHSA) had issued Level 2 (yellow) and Level 3 (amber) Heat Health Alerts for all regions except North East England since 11 July 2021 to warn the public about this heatwave, which they subsequently raised to the highest Level 4 (red) alert for all regions on 18 July 2021 to trigger a national emergency response\"\nThis sentence discusses the July 2022 heatwave (when 40.3°C was recorded on 19 July 2022 and peak heat-related mortality occurred), but the dates for the alerts are incorrectly stated as July 2021. According to official Met Office and UKHSA documentation, the Level 4 Heat Health Alert was issued on 15 July 2022, and the red extreme heat warning was in place from 18-19 July 2022 [[5]](#citation-list). This was the first time a Level 4 alert had been issued since the heatwave plan was introduced in 2004.\n\"On 15 July, the UKHSA increased the Heatwave Alert Level to 4... The Met Office issued its first ever red extreme-heat warning... The warning was in place from 18 to 19 July, with most of England being affected.\" [[6]](#citation-list)\nThe Wikipedia article on the 2022 UK heatwaves, corroborated by Met Office reports, confirms the correct dates were in July 2022, not 2021. The error in the paper appears to be a typographical mistake (2021 instead of 2022) but affects two separate date mentions in the same sentence, suggesting it may not be a simple typo. While this does not affect the quantitative analysis, it creates confusion about the timeline of the unprecedented heat event being discussed.\n\nReferences:\n[5] Met Office (2022). Unprecedented extreme heatwave, July 2022. https://www.metoffice.gov.uk/binaries/content/assets/metofficegovuk/pdf/weather/learn-about/uk-past-events/interesting/2022/2022_03_july_heatwave_v1.pdf\n[6] Wikipedia. 2022 United Kingdom heatwaves. https://en.wikipedia.org/wiki/2022_United_Kingdom_heatwaves", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|GPT|1", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "This paper’s central “compound mortality impact” calculation is not methodologically valid because it adds temperature-attributable deaths and COVID-19 deaths under an explicit independence/additivity assumption, even though the manuscript itself presents evidence and prior literature that the two hazards can interact and share causal pathways; this affects the paper’s core results on heatwaves/cold snaps and the interpretation of “compound” burdens.\n\nThese temperature-related deaths are theoretically independent of COVID-19 deaths because they are calculated from DLNMs that describe the relationships between daily mean temperature and daily all-cause mortality, after COVID-19 mortality has been removed (see Methods).\nRemoving deaths with COVID-19 on the death certificate changes the outcome series, but it does not establish causal independence between temperature and pandemic conditions. COVID-19 can change population vulnerability, healthcare access, and reporting/diagnostic patterns, all of which can modify the temperature–mortality relationship even if COVID-coded deaths are excluded. In addition, some deaths “with COVID-19” could still be partly temperature-triggered, and excluding them can shift attributable fractions rather than eliminate overlap. The claim of theoretical independence is therefore stronger than what the described preprocessing supports. Because the paper’s main “compound” totals depend on this premise, any violation can materially bias compound magnitudes upward or downward. This is a validity issue because it affects the correctness of the main quantitative estimates.\nBy adding temperature-related deaths (with COVID-19 deaths removed prior to calculation) and COVID-19 deaths together to estimate the compound mortality impact, we have assumed that they are independent of each other.\nThis sentence confirms the compound metric is constructed by direct addition, which is only appropriate if the two components are non-overlapping and not interacting in ways that change attribution. The paper does not provide a joint model or an attribution framework that partitions deaths into mutually exclusive components (e.g., main effects plus interaction). Without such a framework, “compound” totals can double count overlapping contributions or miss interaction-driven excess risk. The manuscript later acknowledges potential confounding/effect modification (see next quotes), which directly contradicts treating the components as independent for estimation. In environmental epidemiology, compound-risk questions are typically addressed with interaction terms, stratified associations, or counterfactual decomposition rather than unconditional addition. As written, the compound totals are not a robust estimate of combined burden.\nThese results suggest that COVID-19 may have impacted temperature-related mortality during extreme weather events.\nThis admission implies effect modification or confounding: the temperature–mortality relationship (or baseline risk) differs between COVID and non-COVID periods. If COVID-19 alters temperature-related mortality, then the paper’s additive decomposition into “temperature deaths” plus “COVID deaths” is not stable across periods and cannot be interpreted as two separable components. In that case, a valid compound analysis needs to explicitly model pandemic-related modifiers (e.g., time-varying indicators, healthcare pressure proxies) and quantify uncertainty in the decomposition. Otherwise, the reported compound burdens during heatwaves/cold snaps conflate direct temperature effects, indirect pandemic effects, and their interaction. The figure-based KS test evidence the authors cite supports “difference,” but difference alone does not validate an additive partition. This undermines the conclusions that compound impacts are “clear” and “additive to the first order.”\nBecause of the common risk factors for temperature-related and COVID-19 mortality, disentangling their effects on health and attributing mortality to a single cause is challenging.\nShared risk factors imply that simple cause-wise partitioning is difficult and that overlap is expected, especially in older and comorbid populations. If attribution to a single cause is challenging, then summing two separately attributed quantities and interpreting the sum as “compound” is not automatically justified; it can embed correlated errors and conceptual overlap. This is especially problematic because the temperature component is model-attributable all-cause mortality (after exclusions), while the COVID component is certificate-coded deaths, which are not directly comparable partitions of the same outcome space. The paper does not provide sensitivity analyses showing how compound results change under alternative attribution rules (e.g., including vs excluding COVID-coded deaths in the temperature model). As a result, the compound mortality numbers may be more reflective of a chosen accounting convention than a uniquely defined epidemiologic quantity. That weakens the reliability of the main compound estimates.\n```python\neng_wales_df[\"hw_tempcovid_death_sum_per100k\"] = ((np.array(temp_hw_ds)+np.array(covid_hw_ds))/np.array(reg_pops))*100000\neng_wales_df[\"hw_tempcovid_low_sum_per100k\"] = ((np.array(temp_hw_lw)+np.array(covid_hw_ds))/np.array(reg_pops))*100000\neng_wales_df[\"hw_tempcovid_hgh_sum_per100k\"] = ((np.array(temp_hw_up)+np.array(covid_hw_ds))/np.array(reg_pops))*100000\n\neng_wales_df[\"cs_tempcovid_death_sum_per100k\"] = ((np.array(temp_cs_ds)+np.array(covid_cs_ds))/np.array(reg_pops))*100000    \neng_wales_df[\"cs_tempcovid_low_sum_per100k\"] = ((np.array(temp_cs_lw)+np.array(covid_cs_ds))/np.array(reg_pops))*100000\neng_wales_df[\"cs_tempcovid_hgh_sum_per100k\"] = ((np.array(temp_cs_up)+np.array(covid_cs_ds))/np.array(reg_pops))*100000\n```\nThe code shows the compound estimates are operationally implemented as a direct sum of the two components, with COVID deaths treated as fixed (no uncertainty) and temperature deaths contributing the only uncertainty band. This construction assumes not only independence in expectation but also ignores covariance between estimates, which is precisely what would arise if pandemic conditions modify temperature effects. It also implicitly assumes that COVID deaths are disjoint from temperature-attributable deaths, even though the manuscript acknowledges overlapping risk factors and possible amplification. Because these computed sums are the values mapped in Figure 3 and used to motivate “unprecedented compound health impact,” any conceptual mismatch directly propagates to headline results. A more defensible implementation would estimate joint models (e.g., including pandemic-period indicators and interactions) or provide decomposition bounds under alternative overlap assumptions. As-is, the computation is a major threat to internal validity.\nFor the specific form of Eq. (2), it should be noted that , i.e. the sum of the attributable risk measured for individual exposures is usually higher than their concurrent attributable risk. [[1]](https://pmc.ncbi.nlm.nih.gov/articles/PMC4021419/)\nThis methodological point from the attributable-risk literature directly cautions against summing single-exposure attributable risks and interpreting the result as the “concurrent” burden when exposures (or risk factors) co-occur. The paper’s compound calculation does exactly this—adding separate temperature-attributable mortality and COVID-19 deaths—without establishing that the two components represent non-overlapping counterfactuals. The quote highlights that even under standard attributable-risk definitions, naive additivity tends to overstate the joint burden relative to a properly defined concurrent attributable risk. This is not a minor nuance; it can change both absolute compound numbers and the regional comparisons emphasized in the abstract. The paper would need to formalize the target estimand (e.g., joint counterfactual for temperature and COVID) to justify summation. Without that, the compound results are not clearly interpretable.\nHeat waves and Covid-19 overlap, as this pandemic continues into summer 2021. [[4]](https://pmc.ncbi.nlm.nih.gov/articles/PMC8056477/)\nThis sentence reflects a widely recognized premise in the public-health literature: heat events and COVID-19 can co-occur and stress the same systems and populations. Overlap implies that risks and outcomes during coincident periods are not cleanly separable into two independent components, especially when healthcare capacity and behavioral changes are part of the mechanism. The reviewed paper uses the overlap premise to motivate the study, but then treats the mortality components as independent for its primary compound calculation. This mismatch matters because the paper’s main contribution is claimed to be quantifying “compound” health consequences; overlap is precisely where interactions and shared pathways are expected. The cited review further emphasizes overlapping vulnerable groups and contradictory recommendations, reinforcing that pandemic context can change heat-health outcomes. Therefore, independence should be treated as a strong assumption requiring explicit validation or sensitivity analysis.\n\nReferences:\n[1] [Gasparrini A, Leone M. Attributable risk from distributed lag models. *BMC Medical Research Methodology* (2014).](https://pmc.ncbi.nlm.nih.gov/articles/PMC4021419/)\n[4] [Bose-O’Reilly S, Daanen H, Deering K, et al. COVID-19 and heat waves: New challenges for healthcare systems. *Environmental Research* (2021).](https://pmc.ncbi.nlm.nih.gov/articles/PMC8056477/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|GPT|2", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "The paper’s method for estimating daily heat- and cold-related deaths during 2020–2022 is insufficiently justified and potentially biased because it combines (i) exposure–response functions estimated over 1981–2022 with COVID-era structural changes and (ii) an “average calendar-day mortality” baseline across 1981–2022 (excluding COVID-coded deaths), rather than using observed daily non-COVID deaths in the target period; this threatens the validity of the reported temperature-related death totals and the comparisons to COVID-19.\n\nFor each region in England and Wales, we derive the non-linear association between daily average temperature and daily mortality in the period 1981–2022.\nEstimating a single exposure–response function over a 42-year window implicitly assumes stability of the temperature–mortality relationship after controlling for modeled seasonality and long-term trends. However, the COVID period brought abrupt changes in healthcare access, behaviors, and competing causes, which can violate that stability even if a time spline is included. The paper later notes that COVID-19 may have impacted temperature-related mortality and that deriving associations using only COVID-era data is desirable but not done, which underscores the plausibility of non-stationarity. If the exposure–response function changes during 2020–2022, applying an all-years association to the pandemic period can misattribute deaths to temperature. This is a major issue because the paper’s headline results rely on absolute counts and per-100k rates during 2020–2022. Without sensitivity analyses (e.g., pre-pandemic-only fits vs full-period fits), the robustness of the temperature-attributable totals is unclear.\nSince the 2020–2022 mortality data include COVID-19 deaths, which we want to separate from temperature-related deaths in this study, we remove deaths with COVID-19 on the death certificate from the all-cause mortality data.\nExcluding COVID-coded deaths changes the outcome but does not restore a “business-as-usual” mortality series, because the pandemic affected non-COVID mortality through delayed care, healthcare strain, and behavioral shifts. As a result, the remaining “all-cause (excluding COVID)” deaths in 2020–2022 are still pandemic-influenced and not directly comparable to earlier decades, complicating both association estimation and baseline construction. This matters because the paper uses the resulting series to claim separability and to compare temperature deaths to COVID deaths. If non-COVID mortality spikes during COVID are partly driven by healthcare disruption, temperature attribution may capture pandemic-side effects as temperature effects (or vice versa). Standard time-series DLNM setups can accommodate time-varying confounding, but the paper does not implement explicit pandemic-period controls beyond smooth time terms. The removal step alone is therefore insufficient to support the strong causal interpretation implied by “temperature-related deaths.”\nBased on the observed daily average temperature between 30 January 2020 and 31 December 2022 from HadUK-Grid, the derived mortality risk at each temperature, and the average number of all-cause deaths (excluding COVID-19 deaths) for each calendar day in a year based on the 1981–2022 period, best estimates of heat- and cold-related mortality for each day in the study period are calculated for each region.\nUsing an “average number of deaths for each calendar day” pooled across 1981–2022 imposes a baseline mortality structure that averages over large demographic transitions (aging), healthcare improvements, and secular changes in mortality rates. This can distort attributable numbers in the target period if the true 2020–2022 baseline differs materially from the long-run average, even after accounting for the exposure–response function. The approach effectively smooths away year-specific deviations in mortality that are epidemiologically meaningful during a pandemic, which risks misestimating attributable deaths precisely in the period the paper aims to analyze. It also complicates comparison to COVID-19 death-certificate counts, which are not computed against an averaged baseline. In typical attributable-burden computations for historical periods, the daily counts used in attribution correspond to the observed outcome series at those times, not a multi-decade climatological mean. Because the paper’s core claims depend on absolute counts (e.g., “128,533 excess deaths … attributable to low temperatures”), this baseline choice is a major methodological vulnerability.\n```r\n# EXPECTED MORTALITY SERIES:\n# It is computed as the average mortality for each day of the year \n#   from daily observed deaths, then repeated along the same projection period\n#   of the modelled temperature series.\n\n# first, year-round average deaths per day\ndeathdoy <- tapply(obs$death_allage,as.numeric(format(obs$date,\"%j\")),\n  mean,na.rm=T)[seq(365)]\nwhile(any(isna <- is.na(deathdoy)))\n  deathdoy[isna] <- rowMeans(Lag(deathdoy,c(-1,1)),na.rm=T)[isna]\ndeathexp <- rep(deathdoy,length=nrow(obs))\n```\nThis code reveals that the implementation constructs an expected mortality series by averaging by day-of-year and repeating it—an approach commonly used for projections under “stable population” assumptions. When applied to retrospective estimation during a pandemic, this choice can mute true temporal changes in baseline risk and thus change absolute attributable numbers. It also indicates that attributable deaths are computed against `deathexp` rather than observed daily non-COVID deaths in the focal years, which is a consequential modeling decision, not a mere implementation detail. The comment explicitly frames the method as a projection-style baseline (“repeated along the same projection period”), which is misaligned with the paper’s emphasis on observed 2020–2022 compound crises. If the authors intend this for historical attribution, the paper should justify why a climatological baseline is preferable and quantify sensitivity to alternative baselines (e.g., using observed 2010–2019 or 2020–2022 non-COVID deaths). Without such justification, the reported magnitudes may be artifacts of baseline construction. That affects both validity and the reliability of policy-relevant comparisons.\nFirst, we compute an annual series of total mortality counts as the average for each day of the year from observed daily deaths, thus keeping into account the seasonal structure of the observed mortality series (Figure 3). The annual series is then replicated along the whole projection period. [[2]](https://researchonline.lshtm.ac.uk/id/eprint/4650631/1/VicedoCabrera2019_TutorialEpid_accepted.pdf)\nThis tutorial describes the “average day-of-year mortality replicated forward” construct as part of a framework for projecting future health impacts under climate change scenarios. That contextualizes the baseline choice as a projection assumption to isolate climate effects under stable outcome rates, rather than as the default for estimating historical burdens in periods with major non-climatic shocks. The reviewed paper applies an analogous construct for 2020–2022, a period explicitly characterized by unprecedented pandemic disruption, without providing the projection-style assumptions or discussing their implications. Because the goal here is attribution during an observed crisis, not long-run scenario projection, importing a projection baseline can induce systematic bias. The quote therefore supports that the baseline approach requires stronger justification than provided, especially when the paper’s conclusions hinge on absolute death burdens. A sensitivity analysis aligned with time-series attribution practice would be expected in a study making strong comparative claims against COVID-19 deaths.\nIn time series analyses of environmental factors the outcomes Yt are commonly daily counts, assumed to originate from a so-called overdispersed Poisson distribution with E(Y) = μ, V(Y) = φμ, and a canonical log-link in (1). Usually these include a smooth function of time to capture the effect of confounders changing slowly over time, expressed as seasonality or long-time trends. [[5]](https://pmc.ncbi.nlm.nih.gov/articles/PMC2998707/)\nThis description of standard time-series DLNM practice emphasizes modeling observed daily outcome counts while controlling for time-varying confounding via smooth functions of time and other covariates. The reviewed paper does include a time spline in the regression, but then departs from the usual practice by using a long-run average calendar-day mortality baseline to compute attributable numbers for the focal years. That departure is not necessarily wrong, but it changes the estimand and can affect results substantially when mortality levels shift abruptly, as in 2020–2022. The citation underscores that the canonical DLNM setting is anchored on the observed outcome process at time t, not a climatological mean constructed over decades. In a pandemic-era analysis, preserving the integrity of the observed outcome series (or explicitly modeling deviations) is particularly important for credible attribution. The paper does not clearly articulate why an averaged baseline is preferable for its stated objectives.\n\nReferences:\n[2] [Vicedo-Cabrera AM, Sera F, Gasparrini A. A hands-on tutorial on a modelling framework for projections of climate change impacts on health. *Epidemiology* (2019) (accepted manuscript PDF).](https://researchonline.lshtm.ac.uk/id/eprint/4650631/1/VicedoCabrera2019_TutorialEpid_accepted.pdf)\n[5] [Gasparrini A, Armstrong B, Kenward MG. Distributed lag non-linear models. *Statistics in Medicine* (2010).](https://pmc.ncbi.nlm.nih.gov/articles/PMC2998707/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|GPT|3", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "The conclusion that compound deaths during heatwaves/cold snaps in 2020–2022 are “at least ~2 times higher than the previous decade” is not robust because the reference for 2010–2019 is constructed by scaling an average per-extreme-day burden to 70 days and by using different event-identification criteria across periods; this undermines the paper’s central decade-over-decade amplification claim.\n\nThese numbers are at least ~2 times higher than the previous decade.\nThis is a headline claim in the abstract, so it must be supported by a comparison that isolates the relevant difference (compound co-occurrence vs prior decade temperature extremes) without introducing methodological artifacts. The paper’s own later description shows the previous-decade baseline is not computed from the actual number and severity of heatwave/cold snap days in 2010–2019, but rather from a constructed “same number of days” reference. Such construction can mix together changes in event frequency, event definitions, and population baselines, making the ratio difficult to interpret causally as amplification due to co-occurrence. Additionally, the uncertainty treatment in the ratio is not described; ratios of uncertain quantities should typically propagate uncertainty rather than reporting point ratios alone. Without a like-for-like design (e.g., matching events by temperature intensity or using identical alert-based definitions across periods), the “~2×” figure may not reflect a true doubling of risk. Because this claim motivates preparedness recommendations, weak support is a significant issue.\nThese compound mortality levels are put into context by comparing Figure 3a with Figure 3c, which shows the reference levels of heat-related mortality from 70 heatwave days, calculated from the average of all identified heatwaves in the ten years that preceded COVID-19 (i.e., 2010–2019; see Methods).\nThe comparison is explicitly based on a fixed 70-day reference constructed from an average over identified heatwaves in 2010–2019, then scaled to the study-period count of heatwave days. This does not compare observed 2020–2022 heatwave days to observed 2010–2019 heatwave days under the same event-counting process; it compares a study-period sum to a scaled expectation. If the previous decade had fewer/more heatwave days, different event intensity distributions, or different alert/reporting thresholds, the scaled reference can misrepresent what “the previous decade” actually experienced. The method also implicitly assumes linear scaling of mortality burden with number of days, which may not hold because heat/cold effects are non-linear and depend on intensity, duration, and temporal clustering. The approach therefore risks overstating or understating decade differences depending on how the 70 days are selected in each period. Given that the amplification factor is central to the paper’s narrative, this is a major conclusion-level weakness.\nThroughout this study, we focus on heatwaves and cold snaps when extreme temperatures have the largest mortality impacts. The dates of these events are extracted from the UKHSA Heatwave Mortality Reports and historical Level 3 Cold Health Alerts, as mentioned in the main text. However, these reports and the alerts record available to us only start in 2016, so we find the dates of heatwaves and cold snaps based on the same criteria for the period 2010–2015 for Figure 3. For heatwaves, we find days on which there was a UKHSA Level 3 Heat Health Alert, or days with a mean central England temperature greater than 20°C, plus one day before and after the time period identified through the first two criteria.\nThis methods description confirms that event identification differs across subperiods due to data availability: post-2016 uses alert/report-based extraction, while 2010–2015 uses a hybrid rule that includes a central England temperature threshold and padding days before/after. Even if intended to approximate the same concept, such changes can alter which days are labeled “heatwave” and therefore change the average per-day mortality used to build the 2010–2019 baseline. The choice of “mean central England temperature > 20°C” is not region-specific and may not align with regional alert thresholds, potentially changing the mix of included days relative to 2020–2022. Because the paper then scales an average to exactly 70 days, any mismatch in selection criteria can directly translate into an artificial amplification ratio. A like-for-like comparison would require applying a single, consistent definition to both periods using the same data sources, or quantifying sensitivity across definitions. Without that, the reported fold-changes are not clearly attributable to “co-occurrence with COVID-19” rather than definitional drift.\n```python\n# sums (in magnitudes) in previous decade\neng_wales_df[\"hw_prev_death_70days_per100k\"] = (np.array(temp_hw_prev)/(hwdays*np.array(reg_pops_15)))*(70*100000) # ave heatwave deaths per 100 pop per day * 70 days\neng_wales_df[\"hw_prev_low_70days_per100k\"] = (np.array(temp_hw_plow)/(hwdays*np.array(reg_pops_15)))*(70*100000)\neng_wales_df[\"hw_prev_hgh_70days_per100k\"] = (np.array(temp_hw_pup)/(hwdays*np.array(reg_pops_15)))*(70*100000)\n\neng_wales_df[\"cs_prev_death_70days_per100k\"] = (np.array(temp_cs_prev)/(csdays*np.array(reg_pops_15)))*(70*100000)\neng_wales_df[\"cs_prev_low_70days_per100k\"] = (np.array(temp_cs_plow)/(csdays*np.array(reg_pops_15)))*(70*100000)\neng_wales_df[\"cs_prev_hgh_70days_per100k\"] = (np.array(temp_cs_pup)/(csdays*np.array(reg_pops_15)))*(70*100000)\n\n# ratios of sums (in magnitudes: study period over previous decade\neng_wales_df[\"hw_tempcovid_prev_death_ratio\"] = eng_wales_df[\"hw_tempcovid_death_sum_per100k\"]/eng_wales_df[\"hw_prev_death_70days_per100k\"]\neng_wales_df[\"cs_tempcovid_prev_death_ratio\"] = eng_wales_df[\"cs_tempcovid_death_sum_per100k\"]/eng_wales_df[\"cs_prev_death_70days_per100k\"]\n```\nThe implementation makes the comparison design explicit: it converts the previous-decade total over all identified extreme days into an average-per-extreme-day, then multiplies by 70 to fabricate a 70-day baseline. This approach does not preserve the observed frequency or clustering of extreme days in 2010–2019, nor does it match intensity distributions across decades. It also uses mid-2015 populations (`reg_pops_15`) for the previous decade and mid-2021 populations for the study period, introducing an additional demographic shift into the ratio that is not analyzed. Moreover, the ratio is computed as a single point estimate with no uncertainty propagation, even though both numerator and denominator involve estimated temperature-attributable deaths with uncertainty. As a result, the “2×–3.8×” fold-change statements can be sensitive to definitional and scaling choices rather than reflecting a stable epidemiologic contrast. Given the prominence of this claim, a more defensible comparison would use consistent event definitions and report uncertainty in the ratio.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|GPT|4", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "The paper’s code and data workflow does not enable independent reproduction of the core modeled temperature-attributable mortality series and main figures because key inputs and intermediate outputs are missing and scripts rely on environment-specific absolute paths; this undermines transparency and reproducibility of the primary quantitative results.\n\ndata/ contains COVID-19 mortality and vaccination rate that were open source (links in manuscript) but are no longer available online. Other open souce data that are still available online are not included here, but their links are listed in the manuscript.\nThis statement indicates that some inputs are included because they are no longer available online, but it also acknowledges that other necessary open-source datasets are omitted and must be fetched externally. For reproducibility, the paper must ensure that all required data sources are both accessible and precisely versioned, especially when results depend on historical revisions or dashboard updates. The phrasing does not specify exact dataset versions, retrieval dates (beyond some filenames), or checksums, and it implies reliance on links in the manuscript rather than a complete computational manifest. In addition, the key temperature-attributable mortality estimates depend on all-cause mortality and HadUK-Grid data that are not packaged with the repository, and the repository does not include the intermediate “outputs” used by plotting scripts. This setup makes it difficult for reviewers to validate the reported death totals and confidence intervals. Because the paper’s main contribution is quantitative estimation of burdens, lack of a runnable workflow is a major problem.\n```python\nin_dir = \"/home/bridge/yl17544/papers_repos/EnglandWales_climate_vs_covid_paper/\"\nons_dir = \"/export/anthropocene/array-01/yl17544/ONS/Daily_deaths_by_region_England_Wales/\"\nout_dir = \"/home/bridge/yl17544/plots/EnglandWales_climate_vs_covid/\"\n```\nThe plotting workflow is parameterized by absolute, environment-specific filesystem paths rather than repository-relative paths or a configuration file. This means a third party cannot run the scripts in a clean environment without manual path editing, which prevents straightforward reproduction. It also obscures which exact versions of the upstream datasets are being used, because the data live outside the repository and may change over time. In computational epidemiology, portability is important because small differences in preprocessing can materially change attributable-death estimates. The dependence on external directories is especially problematic here because the paper’s primary results are numerical mortality burdens rather than a purely qualitative analysis. Consequently, the provided code does not meet the transparency needed to validate the headline results.\n```python\ntemp_mort = pd.read_csv(in_dir+\"outputs/daily_attributable_deaths_ER1981-2022_yearround_21dayslag_MMT2to98_nsim100_1981-2022_ONSdata_\"+reg+\".csv\") \n```\nThis line shows that the main plotting scripts require a precomputed daily attributable-deaths file in an `outputs/` directory that is not included with the provided materials. Without these intermediate outputs (or a runnable script that generates them from raw inputs), independent reviewers cannot regenerate the figures or verify the reported totals and confidence intervals. Because these outputs encode the central DLNM-based mortality attribution, their absence blocks validation of the key scientific contribution. Moreover, the compound analyses and decade comparisons rely on these same derived series across multiple scripts, so the missing artifact affects most headline claims. A reproducible release would either include these outputs with clear provenance or provide end-to-end scripts to recreate them deterministically. As it stands, the computational chain is incomplete for reproduction.\n```r\n# mortality and temperature data \n# 1981-2019 (2020 has covid in the earlier data)\nobs1 <- read.csv(paste0(\"/home/bridge/yl17544/papers_repos/UKHSA_monitoring/data/ONS_HadUK-Grid_1981_2020_noleap_\",reg1,\".csv\"),\n                 colClasses=c(\"Date\",NA,NA,NA,NA,NA,\"NULL\",\"NULL\",\"NULL\",\"NULL\",NA,\"NULL\"))\n#obs1 <- read.csv(paste0(\"/home/bridge/yl17544/papers_repos/EnglandWales_climate_vs_covid_paper/data/ONS_HadUK-Grid_25km_LSOApopweighted_1981_2019_noleap_\",reg1,\".csv\"),colClasses=c(\"Date\",NA,NA,NA,NA,NA,\"NULL\",\"NULL\",\"NULL\",\"NULL\",NA,\"NULL\"))\nobs1 <- subset(obs1, date<=\"2019-12-31\")\n# 2020-2022 (removed any deaths with covid on the certificate; ONS data)\nobs2 <- read.csv(paste0(\"/home/bridge/yl17544/papers_repos/EnglandWales_climate_vs_covid_paper/data/ONS_HadUK-Grid_2020_2022_without_covidcert_noleap_\",reg1,\".csv\"),colClasses=c(\"Date\",NA,NA,NA,NA,NA,NA,\"NULL\"))\n#obs2 <- read.csv(paste0(\"/home/bridge/yl17544/papers_repos/EnglandWales_climate_vs_covid_paper/data/ONS_HadUK-Grid_25km_LSOApopweighted_2020_2022_without_covidcert_noleap_\",reg1,\".csv\"), colClasses=c(\"Date\",NA,NA,NA,NA,NA,NA,\"NULL\"))\nobs2 <- subset(obs2, date>=\"2020-01-01\")\n# combine obs in time\nobs <- rbind(obs1, obs2)\n```\nThe core modeling script similarly hard-codes external absolute paths for the temperature–mortality input CSVs rather than reading from the repository’s `data/` directory. Those specific input files are not included in the provided materials, so the DLNMs described in the Methods cannot be refit by an independent reviewer without reconstructing bespoke data processing steps. The file naming suggests custom-prepared ONS+HadUK-Grid merged datasets, which are often the most error-prone part of an epidemiologic pipeline and therefore should be made directly auditable. Because the manuscript’s central estimates (including confidence intervals) depend on these fitted models and their Monte Carlo simulations, missing inputs prevent validation of the results. This is not a minor packaging issue; it blocks end-to-end reproduction. A publication-quality workflow would include either the merged inputs (with documentation) or scripts that deterministically generate them from raw public sources.\nHere, we performed an observational study crossing daily mortality data collected in Portugal (SICO/DGS) with high-resolution temperature series (ERA5/ECMWF), characterizing their relation in the pre-pandemic, and how it aggravated during 2020. [[3]](https://link.springer.com/article/10.1007/s00484-021-02192-z)\nThis external example is relevant because it illustrates the level of transparency typically expected for observational temperature–mortality analyses in the COVID era: explicit specification of mortality and temperature sources and a clear characterization of how the relationship changes during the pandemic year. The reviewed paper cites similar motivations but does not provide a fully reproducible computational path from public sources to its fitted models and attributable deaths series. Without portable scripts and accessible inputs, readers cannot confirm that preprocessing choices (e.g., removal of COVID-coded deaths, handling of leap days, regional aggregation) align with the Methods description. In compound-risk studies, these preprocessing steps are often decisive for results, so reproducibility is essential for trust. The contrast does not imply the reviewed paper must match every detail, but it underscores that clearer, runnable pipelines are feasible and common. Therefore, the current materials fall short of field norms for reproducible computational epidemiology.\n\nReferences:\n[3] [Sousa PM, Trigo RM, Russo A, et al. Heat-related mortality amplified during the COVID-19 pandemic. *International Journal of Biometeorology* (2022).](https://link.springer.com/article/10.1007/s00484-021-02192-z)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "The paper uses a constant 40-year average of daily deaths as the baseline for calculating attributable mortality in 2020-2022, which ignores the significant temporal trends in mortality counts (e.g., recent increases due to aging and the pandemic itself), leading to an underestimation of the absolute mortality burden in the study period.\n\n```r\n# first, year-round average deaths per day\ndeathdoy <- tapply(obs$death_allage,as.numeric(format(obs$date,\"%j\")),\n  mean,na.rm=T)[seq(365)]\nwhile(any(isna <- is.na(deathdoy)))\n  deathdoy[isna] <- rowMeans(Lag(deathdoy,c(-1,1)),na.rm=T)[isna]\ndeathexp <- rep(deathdoy,length=nrow(obs))\n...\n# (5) IMPACT PROJECTIONS:\n# - COMPUTE THE DAILY CONTRIBUTIONS OF ATTRIBUTABLE DEATHS\nan <- (1-exp(-bvarcen%*%coef(red)))*deathexp\n```\nThe code calculates `deathexp` as the average daily deaths for each day of the year across the entire 1981-2022 period, and then repeats this constant seasonal cycle for every year in the projection. This approach assumes that the baseline mortality level in 2020-2022 is the same as the 40-year average. However, annual deaths in England and Wales have exhibited a U-shaped trend, decreasing from ~580,000 in 1981 to ~480,000 in 2011, and then rising back to ~580,000 in 2022 due to population aging [1]. By using the 40-year average (which is pulled down by the lower mortality in the 2000s and 2010s) as the baseline for 2022, the study significantly underestimates the expected number of deaths in 2022, and consequently underestimates the absolute number of temperature-related deaths (calculated as Attributable Fraction × Baseline). Standard DLNM methodologies typically use the observed daily deaths or a time-varying baseline to estimate attributable mortality to avoid such biases [5].\n\nReferences:\n[1] Office for National Statistics (2023). Deaths registered in England and Wales: 2022. https://www.ons.gov.uk/peoplepopulationandcommunity/birthsdeathsandmarriages/deaths/bulletins/deathsregistrationsummarytables/2022\n[5] Gasparrini, A., et al. (2015). Mortality risk attributable to high and low ambient temperature: a multicountry observational study. *The Lancet*, 386(9991), 369-375. https://www.thelancet.com/journals/lancet/article/PIIS0140-6736(14)62114-0", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "The paper incorrectly assumes that removing COVID-19 deaths from the all-cause mortality series makes the remaining temperature-related mortality \"theoretically independent\" of the pandemic, ignoring the significant indirect effects of the pandemic (e.g., healthcare strain, behavioral changes) that likely altered the temperature-mortality relationship for non-COVID causes.\n\n\"These temperature-related deaths are theoretically independent of COVID-19 deaths because they are calculated from DLNMs that describe the relationships between daily mean temperature and daily all-cause mortality, after COVID-19 mortality has been removed (see Methods).\"\nThis claim of independence is methodologically unsound. The \"non-COVID\" mortality during the pandemic was not independent of the pandemic context; it was influenced by factors such as overwhelmed healthcare systems, delayed treatments for chronic conditions, and lockdowns. Recent literature has shown that the risk of heat-related mortality was significantly elevated during the pandemic compared to pre-pandemic periods, even for non-COVID causes, due to these synergistic effects [2]. By using a model trained primarily on pre-pandemic data (1981-2022) to estimate mortality in 2020-2022, the study fails to capture this altered vulnerability, likely underestimating the true heat-related burden during the pandemic.\n\nReferences:\n[2] Ali, E. A., et al. (2025). The overlapping impacts of heat and COVID-19 on mortality in Flanders, Belgium: a time-stratified case-crossover analysis. *Scientific Reports*, 15, 25481. https://doi.org/10.1038/s41598-025-25481-8", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "The paper defines \"compound mortality\" as the simple additive sum of reported COVID-19 deaths and estimated non-COVID temperature-related deaths, which fails to account for the interactive nature of compound risks where one hazard exacerbates the vulnerability to the other.\n\n\"By adding temperature-related deaths (with COVID-19 deaths removed prior to calculation) and COVID-19 deaths together to estimate the compound mortality...\"\nThis additive approach assumes that the two causes are mutually exclusive and non-interacting. However, extreme temperatures can exacerbate COVID-19 transmission and severity (e.g., via indoor crowding or physiological stress), and COVID-19 infection can increase long-term vulnerability to thermal stress [3]. The \"compound\" metric presented is merely the total mortality burden from two separate sources, not a measure of \"compound risk\" as typically understood in disaster risk science, which implies non-linear interactions. The paper should explicitly acknowledge that this additive model likely underestimates the true compound impact if synergistic effects exist.\n\nReferences:\n[3] Phillips, C. A., et al. (2020). Compound climate risks in the COVID-19 pandemic. *Nature Climate Change*, 10(7), 586-588. https://www.nature.com/articles/s41558-020-0804-2", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "The study does not account for the \"harvesting\" or mortality displacement effect where the high mortality from COVID-19 (targeting the most vulnerable) may have depleted the pool of susceptible individuals, potentially leading to an overestimation of the subsequent temperature-related mortality in the \"non-COVID\" series when using a historical model.\n\n\"We estimate the mortality attributable to short-term heat and cold events... in England and Wales in the period 2020-2022, during which the COVID-19 pandemic peaked in terms of mortality.\"\nThe \"harvesting\" effect is a well-documented phenomenon where a high-mortality event removes the frailest individuals, leading to a temporary reduction in mortality in the subsequent period [4]. Since COVID-19 disproportionately affected the elderly and those with comorbidities (who are also most vulnerable to temperature extremes), the remaining \"non-COVID\" population in 2020-2022 might have been, on average, less vulnerable to heat/cold than the historical average. The DLNM, trained on 40 years of data with a \"normal\" population structure, would overestimate the temperature-related deaths when applied to this \"survivor\" population, introducing a bias that contradicts the paper's claim of high temperature-related mortality.\n\nReferences:\n[4] Toulemon, L., & Barbieri, M. (2008). The mortality impact of the August 2003 heat wave in France: investigating the 'harvesting' effect and other long-term consequences. *Population Studies*, 62(1), 39-53. https://www.tandfonline.com/doi/abs/10.1080/00324720701804249", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Gemini|5", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "The comparison of \"compound\" mortality in 2020-2022 (Heat + COVID) with \"temperature-related\" mortality in 2010-2019 (Heat only) is largely driven by the addition of a new cause of death (COVID-19) and does not provide meaningful insight into how the co-occurrence altered the burden beyond the simple addition of the pandemic.\n\n\"In other words, demand on regional health services was 1.7 (London) to 3.8-fold (North West England) when extreme heat coincided with COVID-19 in the study period, compared to the previous decade.\"\nThis finding is mathematically inevitable given that COVID-19 added a significant number of deaths (approx. 200,000) to the 2020-2022 period, while 2010-2019 had zero COVID-19 deaths. The comparison essentially states that \"Pandemic + Heat > Heat alone,\" which is a trivial conclusion. A more scientifically significant comparison would be to assess whether the *excess mortality from all causes* during heatwaves in 2020-2022 was greater than the sum of *expected* COVID deaths and *expected* heat deaths (based on historical rates), which would reveal the true \"compound\" or interactive effect.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "[Results] L122-123. I would delete “in distributed lag non-linear models (DLNMs) for health modelling”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "[Results] L226-228 and L239-240. The authors use a mortality ratio as an indicator of health services demand. I am not sure whether this is a valid and recognized indicator for monitoring health services demand. I would rewrite the sentences under consideration.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "[Results] Figure 3. I would add a third row of maps showing the ratio a/c and b/d, and reference these new maps in the text (L226-228 [heat] and L239-240 [cold]).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "[Results] L250-253. I think the sentence should read: “the 250 extreme temperature events that co-occurred with COVID-19 have different distributions (black solid lines) from the events that occurred without COVID-19 co-occurrence (grey dashed lines)”. Moreover, I would replace the term “lines” by “ellipse contour”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "[Discussions] L296-303. It has been reported in the literature that air conditioning and heating are effective adaptive measures to high and low temperatures:\n\n- Sera, F. et al. Air conditioning and heat-related mortality: A multi-country longitudinal study. Epidemiology 31, 779–787 (2020).\n\n- Achebak, H. et al. Drivers of the time-varying heat-cold-mortality association in Spain: A longitudinal observational study. Environ. Int. 182, 108284 (2023).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "[Methods] I think the methods should be reported using the past tense.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "[Methods] Mortality data were not available at a finer geographical scale? (eg, Counties)", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "[Methods] What is the spatial resolution of the HadUK-Grid?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Human_1|10", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "[Methods] Some modelling choices are not sufficiently justified (eg, number degrees of freedom [DF] for seasonality) and the sensitivity analysis is missing (eg, DF for seasonality, internal knots for the exposure-response function).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Human_1|11", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "[Methods] L386-398. The authors could improve the description the time-series regression model, and especially, the DLNM.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Human_1|12", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "[Methods] I would include the formula of the time-series regression model.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Human_1|13", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "[Methods] I would report the region-specific temperature-mortality association (ie, risk curves) in the Supplement.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Human_1|14", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "[Methods] L410-411. How did you calculate heat- and cold-related mortality?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "Line 61: Suggest replacing \"social restriction\" with \"physical distancing.\"", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "Lines 165-167: The statement \"These results demonstrate that even during a global pandemic that dominated everyone’s lives, heat and cold were a comparable but arguably much more under-reported killer than COVID-19\" appears unsupported by the data. The data indicates that, over the entire period, COVID-19 mortality generally exceeded mortality attributable to extreme temperatures in UK regions, with the exception of South West England. Therefore, the suggestion of under-reporting seems unfounded.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "Lines 319-325: The authors rightly acknowledged that extreme temperatures mainly affect the health of older people, and this holds true for COVID-19 as well, as it tends to be more severe in the older population. However, the study did not consider the varying age structures across UK regions. For instance, in 2021, the median age in the South West was 44 years, while in London, it was 35 years (source: https://www.ons.gov.uk/peoplepopulationandcommunity/populationandmigration/populationestimates/bulletins/populationandhouseholdestimatesenglandandwales/census2021unroundeddata). This may introduce bias into the comparison of excess mortality across UK regions. Therefore, it is recommended that results be presented as age-adjusted rates.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "In the comparison between several extreme weather events and their effect, authors should emphasize that in low-capacity settings such as Pakistan and Africa – where vital registration is very lacking, the figures aren’t comparable to UK estimated excess deaths where vital registration is complete and causes of death are properly attributed. See estimates of death registration completeness by UNSD https://unstats.un.org/unsd/demographic-social/crvs/ and proper attribution of deaths by https://doi.org/10.1186/s12911-021-01501-1.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "In the paragraph on covid-19 deaths, authors cite 7M deaths, but this is only officially reported deaths, with excess deaths from covid being much higher, especially in developing countries. Seeing that this is a paper on excess mortality, this is highly relevant. Authors can cite the WHO’s excess deaths estimate study on this: https://www.nature.com/articles/s41586-022-05522-2.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "When discussing results for all of England & Wales (i.e. figure 1), it’s unclear to me if the results are the sum of the regional-level models or a model fitted on the total itself.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "Authors compare climate deaths per capita by region for 2010-2019 vs. study period (2020-2022), but in the Methods section cite regional-population counts only for 2021. What population counts were used for 2010-2019? This should be added and more clearly described.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|60|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb60", "comment": "Authors rightfully point out that cold-related deaths are harder to ascertain than heat-related deaths, and that they come with a longer lag. Another important reason is that low-temperatures carry with it many ILI and respiratory diseases, making it hard to distinguish between these factors.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Claude|1", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "The paper contains incorrect SSP scenario naming in Figure 3, labeling scenarios as \"SSP1-2.5\" and \"SSP3-7.5\" which do not exist in the CMIP6 framework, raising concerns about whether the correct climate scenarios were actually used in the analysis.\n\nFrom Figure 3 visual inspection: \"(a) SSP1-2.5\", \"(c) SSP3-7.5\"\nThese scenario labels are incorrect. The standard CMIP6 Tier 1 scenarios are SSP1-2.6, SSP2-4.5, SSP3-7.0, and SSP5-8.5, as established by ScenarioMIP. The radiative forcing values (2.6, 4.5, 7.0, 8.5 W/m²) correspond to specific emission trajectories. \"SSP1-2.5\" and \"SSP3-7.5\" do not exist in the CMIP6 framework. This discrepancy indicates either a typographical error or potential confusion about which scenarios were actually employed, which is critical given that the entire study relies on CMIP6 projections.\n\"The sixth Coupled Model Intercomparison Project (CMIP6) considers socioeconomic development as well as climate change factors and can reflect the interaction between them, providing the possibility to effectively predict DAPP in the future.\"\nThe paper claims to use CMIP6, yet the scenario naming in Figure 3 does not match CMIP6 conventions. According to the IPCC AR6 and multiple authoritative sources, the standard high-priority CMIP6 scenarios are SSP1-2.6, SSP2-4.5, SSP3-7.0, and SSP5-8.5. This naming inconsistency raises questions about methodological rigor and whether the correct data sources were used.\n\"ClimateData.ca hosts CMIP6 projections based on four SSP scenarios (SSP1-2.6, SSP2-4.5, SSP3-7.0 and SSP5-8.5)\" and \"ScenarioMIP identifies four priority (tier-1) scenarios...SSP1-2.6 for sustainable pathways, SSP2-4.5 for middle-of-the-road, SSP3-7.0 for regional rivalry, and SSP5-8.5 for fossil\" [[1]](#citation-1)\nThe authoritative CMIP6 documentation from multiple sources confirms the standard scenario nomenclature. The paper's use of non-standard names (SSP1-2.5, SSP3-7.5) in Figure 3 contradicts these established conventions and may indicate either erroneous data labeling or actual use of incorrect scenarios, either of which undermines confidence in the results.\n\nReferences:\n[1] [Climate Scenarios Canada - CMIP6 and Shared Socio-economic Pathways overview](https://climate-scenarios.canada.ca/?page=cmip6-overview-notes) and [ClimateData.ca - Understanding Shared Socio-economic Pathways (SSPs)](https://climatedata.ca/resource/understanding-shared-socio-economic-pathways-ssps/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Claude|2", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "The paper claims to account for provincial differences in disease mortality projections but fails to adequately explain how the GBD forecasting model (which provides national-level predictions) was adapted or downscaled to generate provincial-level mortality forecasts.\n\n\"In addition, for future disease mortality, we used the GBD development prediction model to estimate it according to the study by Foreman et al.\"\nForeman et al. (2018) developed forecasts for 195 countries and territories, not subnational units. The paper does not explain how these national-level methods or outputs were modified to generate provincial-scale disease mortality predictions for China's 31 provinces. This methodological gap is significant because the study claims its novelty lies in capturing provincial differences.\n\"Since previous studies did not fully consider the differences on drivers of deaths attributable to PM₂.₅ pollution (DAPP) (i.e., socioeconomic factors, climate factors, and disease mortalities) among provinces in China, the impact of future population aging on DAPP cannot be comprehensively and objectively estimated.\"\nThe paper explicitly criticizes previous studies for not capturing provincial differences in disease mortality, yet it does not provide sufficient detail on how its own provincial mortality projections were derived. The GBD forecasting methodology described in Foreman et al. (2018) uses sociodemographic indices and risk factors at the country level, not provincial level.\n\"The methodology incorporated several distinct sets of input data and processing steps... We then combined these fractional source contributions with newly available high-resolution exposure estimates for both 2017 and 2019\" [[2]](#citation-2)\nThe GBD MAPS study and related work demonstrate the complexity of downscaling health burden estimates from national to subnational levels. The reviewed paper does not provide comparable methodological detail for its provincial mortality projections, leaving it unclear whether the provincial estimates are based on actual GBD provincial data, interpolated from national forecasts, or derived through another unstated method.\n\nReferences:\n[2] [McDuffie et al. (2021). Global Burden of Disease from Major Air Pollution Sources (GBD MAPS)](https://pmc.ncbi.nlm.nih.gov/articles/PMC9501767/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Claude|3", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "The paper validates its DAPP estimates only through national-level Pearson correlations, which does not verify the accuracy of provincial-scale estimates that the study claims as its methodological contribution over prior work.\n\n\"We used Pearson's correlation to verify the reliability of the results (Appendix Figure S3). Specifically, we compared the results obtained in Equation (1) with the estimates calculated by Yue et al based on the Integrated Exposure Response (IER) model, the estimates calculated by Geng et al based on the Global Exposure Mortality Model (GEMM), and the estimates calculated Yin et al\"\nThe validation compares aggregate national-level estimates with previous studies. This does not validate the provincial-level estimates, which is the key claimed methodological advancement. Provincial estimates could have significant errors that are masked when aggregated to national totals.\n\"This scenario setting does not take into account the differences in PM₂.₅ concentration changes in different provinces in the future... the population data used by Liu et al are also national-scale data, ignoring regional differences in population aging in China\"\nThe paper criticizes previous studies for ignoring provincial differences, yet its own validation approach does not demonstrate that provincial estimates are accurate. A proper validation would compare provincial DAPP estimates against provincial-level data from GBD or other independent sources, rather than only national aggregates.\n\"Our findings show that premature deaths decreased by 85,500 (95% CI: 81,300–89,700) after 2013... However, the Gini coefficient for health burden disparities rose by 19.7%, indicating an increasing concentration of health risks\" [[3]](#citation-3)\nOther studies examining PM2.5-related mortality in China have validated regional variations and disparities using provincial data. The reviewed paper's reliance on national-level correlation as the sole validation method is insufficient given its provincial-level claims and falls short of validation approaches used in comparable studies.\n\nReferences:\n[3] [Nature Communications Earth & Environment (2026). Inequality in PM2.5 Exposure and Health burden attributable in China](https://www.nature.com/articles/s44168-026-00340-y)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Claude|4", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "The paper describes combining uncertainties from exposure-response functions, PM2.5 concentrations, and disease mortality projections, but the methodology for propagating these uncertainties appears incomplete and may not account for correlations between uncertainty sources.\n\n\"the upper and lower bounds of the confidence interval for DAPP in this study were determined by the upper and lower bounds of the exposure response function and the upper and lower bounds of confidence intervals for PM₂.₅ concentration and disease mortality\"\nThis description suggests that confidence intervals may have been combined by using the upper or lower bounds of each source simultaneously. However, this approach does not constitute proper uncertainty propagation unless Monte Carlo methods or analytical error propagation formulas are applied. If uncertainties are correlated or if they propagate nonlinearly through the DAPP calculation (Equation 1), this approach could significantly underestimate or mischaracterize total uncertainty.\n\"This study assumed that the simulation results of each model conformed to the t-distribution, and the 95% confidence interval of the PM₂.₅ concentration can be expressed as...\"\nThe assumption of t-distribution for PM2.5 model ensemble spread is reasonable for characterizing model uncertainty, but the paper does not explain how this PM2.5 uncertainty interacts with the uncertainty in the nonlinear exposure-response function and the disease mortality prediction uncertainty. Proper uncertainty propagation would require joint sampling or analytical methods that account for these interactions.\n\"For PM2.5, we consider two different exposure models... Both models include quinquennial age-dependent exposure relationships... We use the MR-BRT and GEMM splines for RR as a function of disease and PM2.5 exposure provided by McDuffie et al., which include CIs that account for uncertainty in TMRELs\" [[4]](#citation-4)\nThe GBD methodology uses sophisticated approaches for propagating uncertainty, including drawing samples from posterior distributions and computing credible intervals from multiple draws. The reviewed paper's description of uncertainty propagation lacks this level of methodological detail, suggesting the reported confidence intervals may not fully capture the compounded uncertainties from all sources.\n\nReferences:\n[4] [Pai et al. (2024). Estimating future climate change impacts on human mortality, PNAS](https://pmc.ncbi.nlm.nih.gov/articles/PMC11441565/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Claude|5", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "The paper does not adequately discuss or correct for the known systematic underestimation of PM2.5 concentrations by CMIP6 models, particularly in highly polluted regions like China, which could bias DAPP projections.\n\n\"We calculated future the PM₂.₅ concentration in China based on empirical formulas and future pollutant concentration data\"\nThe paper mentions using CMIP6 pollutant concentration data but does not discuss bias correction. Multiple studies have documented that CMIP6 models systematically underestimate surface PM2.5 concentrations, particularly in regions with high pollution levels like East Asia. This could lead to underestimation of future DAPP if not addressed.\n\"Turnock et al. reported that CMIP6 models underestimate the historical surface PM2.5 worldwide and projected the decrease of PM2.5 in future scenarios containing strong air quality and climate mitigation measures\" [[5]](#citation-5)\nThe established literature, including Turnock et al. (2020), demonstrates that CMIP6 models underestimate historical PM2.5 concentrations globally. For China specifically, where PM2.5 levels are among the highest in the world, this underestimation bias could be substantial. The reviewed paper does not discuss how this known bias might affect its projections or apply bias correction methods commonly used in such studies.\n\"Disagreements in the projection of future changes to regional surface PM2.5 concentrations between individual CMIP6 models could be attributed to differences in the complexity of the aerosol schemes implemented within models\" [[5]](#citation-5)\nThe intermodel variability in CMIP6 PM2.5 projections, as noted by Turnock et al., is driven by differences in aerosol representations across models. The reviewed paper uses 11 CMIP6 models but does not discuss which specific models were selected or whether the selection considered model performance in reproducing historical PM2.5 over China. This lack of discussion about model selection and bias correction is a methodological limitation.\n\nReferences:\n[5] [Turnock et al. (2020). Historical and future changes in air pollutants from CMIP6 models. Atmospheric Chemistry and Physics, 20, 14547-14579](https://acp.copernicus.org/articles/20/14547/2020/)", "reviewer_type": "ai", "label": "error", "error_type": "Neglect", "label_origin": "expert+llm-filter"}
{"id": "prb|61|GPT|1", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "This paper’s PM\\$_{2.5}$\\ concentration reconstruction from CMIP6 aerosol components is likely systematically biased because it omits nitrate and uses an oversimplified ammonium calculation, undermining the validity of the exposure estimates that drive all downstream DAPP projections and driver attributions.\n\n\"Specifically, referring to the study of Chowdhury et al\\$^{53}$ and Van Donkelaar et al\\$^{54}$, we used the empirical formula to estimate PM\\$_{2.5}$\\ concentration:\\n\\n\\[\\n\\text{PM}_{2.5} = \\text{BC} + \\text{OA} + SO_4 + NH_4 + 0.25 \\times SS + 0.1 \\times dust\\n\\] (3)\"\nThis formula operationalizes the paper’s central exposure pathway by summing only BC, OA, sulfate, an inferred ammonium term, and scaled sea salt and dust. Notably, it does not include nitrate (NO\\$_3^-$), despite nitrate being a major PM\\$_{2.5}$\\ constituent in many polluted regions and seasons. Because DAPP is computed from relative risk as a function of PM\\$_{2.5}$\\ exposure, any systematic underestimation of PM\\$_{2.5}$\\ will propagate nonlinearly into attributable deaths and could change both national totals and the decomposition results. The omission is methodological rather than cosmetic: it changes the mass concentration that is fed into the exposure–response function. Common practice in chemical transport modeling and observation-based composition studies is to treat nitrate and ammonium (often as ammonium nitrate) as core PM\\$_{2.5}$\\ components, especially where nitrate has increased as sulfate declines. Without demonstrating that nitrate is negligible in their CMIP6-based reconstruction for China, the paper’s exposure estimates are not well supported.\n\"\\[\\nNH_4 = \\frac{(36 \\times SO_4)}{96}\\n\\] (4)\"\nThis equation implicitly assumes ammonium is determined solely by sulfate stoichiometry (ammonium sulfate) and does not account for ammonium nitrate formation. In regions like northern China, nitrate and ammonium can co-vary strongly during haze events, and ammonium can be allocated between sulfate and nitrate depending on chemical regime. The paper’s stated approach therefore risks misallocating aerosol mass and misrepresenting how PM\\$_{2.5}$\\ evolves under different emissions scenarios. Because the paper later interprets scenario differences in PM\\$_{2.5}$\\ as a key driver of changing DAPP, chemical simplifications that systematically distort PM\\$_{2.5}$\\ mass threaten the validity of conclusions about mitigation benefits. The issue is amplified by the paper’s reliance on model-to-satellite calibration (Eq. 5), because a biased “model PM\\$_{2.5}$\\” trend will bias the calibrated trend as well. A defensible approach would either include nitrate explicitly or justify, using model outputs/observations, that nitrate is consistently negligible for the study region and period.\n\"Sulfate (SO42-), Nitrate (NO3-), and Ammonium (NH4+) are three main components of WSI.\" [[3]](#ref3)\nThis sentence from an observational study makes explicit that nitrate and ammonium are among the main inorganic contributors to PM\\$_{2.5}$\\ mass (via water-soluble ions). The paper under review builds PM\\$_{2.5}$\\ from a subset of components and infers ammonium only from sulfate, which is inconsistent with the empirical understanding that nitrate is often co-dominant with sulfate in PM\\$_{2.5}$\\. While the external study is focused on Beijing haze, it highlights a broader compositional reality that is especially relevant for China, where secondary inorganic aerosol is a major PM\\$_{2.5}$\\ fraction. If nitrate is a main component in heavily polluted conditions, omitting it can substantially bias PM\\$_{2.5}$\\ exposure and hence DAPP. This matters for projections because the paper’s scenarios alter emissions and chemistry drivers in ways that can change nitrate formation, so the omission is not merely a constant offset. The paper does not provide sensitivity analyses or validation against observed/speciated PM\\$_{2.5}$\\ that would alleviate this concern.\n\"Our study indicates that nitrate has become the most important component of WSI in PM2.5 and is driving the rapid growth of PM2.5 concentrations during heavy pollution episodes in Beijing.\" [[3]](#ref3)\nThis sentence provides concrete evidence that nitrate can dominate PM\\$_{2.5}$\\ growth during severe pollution episodes in China, reinforcing that nitrate is not a minor detail. The paper’s exposure reconstruction would, by construction, be unable to capture nitrate-driven PM\\$_{2.5}$\\ increases or changes in nitrate’s relative contribution across scenarios. Because exposure–response relationships for PM\\$_{2.5}$\\ are nonlinear, missing high-exposure episodes or underestimating their magnitude can disproportionately change attributable mortality estimates. Even if the paper focuses on provincial averages and longer time windows, compositional biases can still shift annual mean concentrations enough to affect DAPP materially. This undermines confidence in the magnitude of projected declines in DAPP attributed to PM\\$_{2.5}$\\ improvements. The paper would need to demonstrate that its component-based formula yields realistic PM\\$_{2.5}$\\ levels and trends (including nitrate-rich regimes) to support its main quantitative claims.\n\nReferences:\n[3] <a id=\"ref3\"></a>[Nitrate dominates the chemical composition of PM2.5 during haze event in Beijing, China. (PubMed: 31466166)](https://pubmed.ncbi.nlm.nih.gov/31466166/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|GPT|2", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "This paper’s methodology for projecting disease mortality and applying the GBD exposure–response function lacks the necessary operational details (drivers, coefficients, and risk-curve specifications), preventing independent reproduction of DAPP results and weakening confidence in the robustness of the projected scenario differences.\n\n\"In addition, for future disease mortality, we used the GBD development prediction model to estimate it according to the study by Foreman et al\\$^{55}$.\"\nThis sentence claims reliance on a specific, complex forecasting framework, but the manuscript does not provide enough implementation detail to allow replication at the provincial level. In practice, applying the Foreman et al. framework requires specifying which covariates/drivers are used, how they are measured for each province, and how coefficients are obtained or transferred. The paper presents generic equations but does not provide parameter values (\\(\\beta\\), \\(\\theta_a\\), \\(\\alpha\\)) or the underlying time series used to fit the models. Without these, other researchers cannot reproduce the mortality trajectories that materially influence DAPP projections and decomposition results. This is not a minor documentation issue: mortality projections are one of the four principal drivers the paper decomposes, so missing details directly obstruct verification of the paper’s central claim that aging offsets air-quality and health-care improvements. Transparent reporting is standard in forecasting studies precisely because different modelling choices can yield materially different mortality trends.\n\"According to the model, the following relationship is satisfied between disease mortality and its drivers:\\n\\n\\[\\nln(m) \\sim N(\\hat{y} + \\hat{\\epsilon}, \\sigma)\\n\\] (6)\\n\\n\\[\\n\\hat{y} = \\beta_1 SDI_{<0.8} + \\beta_2 SDI_{\\geq0.8} + \\theta_a t + \\alpha_{la}\\n\\] (7)\\n\\n\\[\\n\\hat{\\epsilon} = ARIMA\\left( \\epsilon_{history} \\right)\\n\\] (8)\"\nThese equations are too high-level to be reproducible without specifying the exact definition of SDI in the study (including its components and provincial time series), the thresholding rule application, the estimation procedure for coefficients, and the ARIMA model orders/selection. The paper also does not clarify whether these equations are fitted separately for each cause-age-province combination or pooled, which determines forecast behavior and uncertainty. Moreover, the manuscript does not indicate how risk factors (beyond SDI) are incorporated, even though the cited forecasting framework is typically risk-factor driven and scenario-based. Because DAPP is computed as a product involving cause- and age-specific mortality rates, small methodological differences in mortality projection can lead to large differences in attributable deaths over time. This lack of specificity materially affects both reproduccing numerical results and assessing robustness of scenario comparisons. As a result, the mortality component of the decomposition analysis cannot be independently verified.\n\"Our modelling framework used data from the GBD 2016 study to systematically account for the relationships between risk factors and health outcomes for 79 independent drivers of health.\" [[4]](#ref4)\nThis sentence from Foreman et al. clarifies that the referenced approach is not just a simple SDI-plus-trend model; it explicitly incorporates a large set of drivers linking risk factors to outcomes. The manuscript under review does not describe which of these drivers are used (if any), how they are mapped to provincial data, or how alternative SSP scenarios influence them, creating a mismatch between the cited method’s requirements and the information provided. If the paper is using a materially simplified variant, it should clearly specify the simplifications and justify them, because simplification can change projected mortality trends and uncertainties. This matters for the paper’s conclusions because it attributes a large share of DAPP reductions to declining disease mortality and then argues that aging offsets these gains. Without a transparent, reproducible mortality projection consistent with the cited platform, the driver decomposition is difficult to trust quantitatively. The quote thus supports that essential methodological details are missing relative to common practice in the referenced forecasting literature.\n\"Theoretical Minimum Risk Exposure Level (TMREL) Draws [CSV]\" [[5]](#ref5)\nThis excerpt from the official GBD 2019 particulate matter risk-curve record indicates that applying GBD-style PM\\$_{2.5}$\\ risk functions requires specifying a theoretical minimum risk exposure level (TMREL), not only an exposure–response curve shape. In the manuscript, RR is referenced via MR-BRT and used to form PAF, but the operational details of how exposure is translated into RR (including any TMREL choice and curve parameters) are not spelled out. Without specifying these inputs, two implementations can yield different attributable fractions even when using the same exposure data. This creates an avoidable reproducibility gap for a core part of the risk assessment pipeline. The issue is particularly important in future scenarios because changes in exposure distributions near TMREL can strongly affect incremental attributable risk. The evidence supports that key, implementation-critical specifications expected in GBD-style analyses are absent.\n\nReferences:\n[4] <a id=\"ref4\"></a>[Foreman, K. J. et al. Forecasting life expectancy, years of life lost, and all-cause and cause-specific mortality for 250 causes of death… *The Lancet* (2018). (PubMed: 30340847)](https://pubmed.ncbi.nlm.nih.gov/30340847/)\n[5] <a id=\"ref5\"></a>[IHME GHDx: Global Burden of Disease Study 2019 (GBD 2019) Particulate Matter Risk Curves (2021)](https://ghdx.healthdata.org/record/ihme-data/global-burden-disease-study-2019-gbd-2019-particulate-matter-risk-curves)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|GPT|3", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "This paper’s claimed verification of historical DAPP estimates is methodologically inadequate because it relies on Pearson correlation against other studies (which use different risk functions) rather than assessing agreement or bias, weakening the validity of the paper’s reliability claims.\n\n\"We used Pearson's correlation to verify the reliability of the results (Appendix Figure S3).\"\nPearson correlation measures linear association, not whether two methods agree in absolute magnitude, which is crucial for burden-of-disease estimates. Two series can be highly correlated while differing systematically by large offsets or scale factors, leading to misleading comfort about accuracy. Because the paper’s downstream claims hinge on the magnitude of DAPP and its changes over time, demonstrating agreement (e.g., via calibration plots, error metrics, or Bland–Altman-style analyses) is more appropriate than correlation alone. Moreover, the paper does not report the correlation values, sample size, or whether the comparison is done at national, provincial, or annual resolution in the main text, limiting interpretability of the “verification.” In epidemiological risk assessment, validation commonly focuses on absolute error and uncertainty coverage, not just trend similarity. Without an agreement-focused validation, the paper’s assertion that results are “reliable” remains weakly supported.\n\"Specifically, we compared the results obtained in Equation (1) with the estimates calculated by Yue et al\\$^{22}$ based on the Integrated Exposure Response (IER) model, the estimates calculated by Geng et al\\$^{14}$ based on the Global Exposure Mortality Model (GEMM)\"\nThis comparison mixes estimates derived from different exposure–response frameworks (IER vs GEMM vs the paper’s stated MR-BRT/GBD approach), which can legitimately produce different attributable mortality even given identical exposures. As a result, correlation with those estimates is not an unambiguous test of correctness; it can only show broad co-movement, which may arise from shared inputs like population or baseline mortality trends. A meaningful validation would either compare against a ground-truth proxy (e.g., monitored PM\\$_{2.5}$\\ exposures and independently estimated attributable mortality) or evaluate whether the paper’s method reproduces a benchmark implementation under controlled assumptions. The paper itself acknowledges systematic differences across risk functions elsewhere (e.g., discussing GEMM yielding higher RR), underscoring that correlation against heterogeneous models is not a definitive check. Without careful harmonization of counterfactual exposure, cause mapping, age groups, and RR functions, the comparison cannot establish accuracy. Thus, the “verification” step does not adequately support the paper’s confidence in its historical estimates.\n\"Such investigations are often analysed inappropriately, notably by using correlation coefficients. The use of correlation is misleading.\" [[2]](#ref2)\nThis statement from Bland and Altman directly addresses the core statistical problem in using correlation as a validation metric. The paper under review does exactly what this methodological guidance warns against: using correlation to argue that two measurement/estimation methods “agree” or that one is “reliable.” In burden estimation, the question is not merely whether estimates rise and fall together, but whether the estimated levels are sufficiently close for policy-relevant conclusions. The cited guidance also implies that alternative approaches (graphical agreement analyses and simple calculations of differences) are more appropriate when comparing methods. Because the paper’s principal results are quantitative (tens to hundreds of thousands of deaths), misleading validation could materially affect confidence in the reported magnitudes. This evidence therefore supports that the paper’s validation approach is insufficient by common methodological standards.\n\nReferences:\n[2] <a id=\"ref2\"></a>[Bland, J. M. & Altman, D. G. Statistical methods for assessing agreement between two methods of clinical measurement. *The Lancet* (1986). (PubMed: 2868172)](https://pubmed.ncbi.nlm.nih.gov/2868172/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|GPT|4", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "This paper’s uncertainty quantification for PM\\$_{2.5}$\\ (and therefore DAPP) is statistically fragile because it treats an ensemble of CMIP6 models as t-distributed draws and uses a t-based confidence interval, despite well-known dependence and “ensemble-of-opportunity” properties of multi-model climate ensembles.\n\n\"The confidence interval of the PM\\(_{2.5}\\) concentration was determined by the difference of 11 models in the CMIP6 dataset\\$^{53}$. This study assumed that the simulation results of each model conformed to the t-distribution\\$^{46}$, and the 95% confidence interval of the PM\\(_{2.5}\\) concentration can be expressed as:\\n\\n\\[\\nC_{CI} = Con_{mean} \\pm \\sqrt{Var(C)} * T_{95\\%}(n-1)\\n\\]\"\nThe manuscript equates inter-model spread with a frequentist confidence interval derived from a t-statistic, which implicitly presumes a sampling model where members are exchangeable draws from a distribution with well-defined degrees of freedom. CMIP6 models are not independent random draws from a known population; they share code, parameterizations, and tuning practices, and they are contributed by modeling centers with varying but non-random inclusion criteria. Treating them as t-distributed draws can misstate uncertainty, often giving an appearance of statistical rigor (a “95% CI”) without a defensible probabilistic interpretation. This matters because the paper’s headline results repeatedly report 95% confidence intervals for DAPP changes, and these are partially driven by the PM\\$_{2.5}$\\ uncertainty term. If the uncertainty model is mis-specified, the width and even the meaning of those intervals are unclear, weakening policy-relevant conclusions about projected reductions or increases. A more standard approach would treat model spread as an ensemble range (not a CI), explore structural uncertainty via multiple methods, and/or use probabilistic frameworks justified by model evaluation and dependence structure.\n\"for MMEs like CMIP3, the models are sampled neither randomly nor systematically but the ensemble is determined by whichever modeling center had interest and resources to contribute.\" [[1]](#ref1)\nThis sentence explains why a multi-model ensemble generally lacks a clean statistical sampling interpretation. The paper under review effectively treats the CMIP6 ensemble as if it were a random sample enabling t-based inference, which conflicts with the characterization above. If models are selected by opportunity rather than a defined sampling protocol, then “degrees of freedom” and classical confidence intervals are not well grounded. This is directly relevant because the paper uses only 11 models and then applies a parametric CI formula, implying a probabilistic meaning that the ensemble construction does not support. In such contexts, best practice is to be explicit that inter-model spread is not a calibrated probability distribution unless additional assumptions or weighting/independence corrections are justified. The evidence thus supports that the paper’s CI construction is not aligned with established interpretations of climate multi-model ensembles.\n\"models are dependent and share biases and the assumption of independence made in some studies is likely to lead to overconfidence, if the uncertainty is measured by the standard error of the ensemble means (inversely proportional to the square root of the ensemble size).\" [[1]](#ref1)\nThis sentence highlights a concrete failure mode: overstating confidence when models are treated as independent. The paper’s t-interval approach similarly compresses uncertainty into a “standard error”-like form derived from ensemble variance and a t-statistic, which is vulnerable to exactly this overconfidence problem. If model outputs are correlated, the effective sample size is smaller than 11, so a naive t-based CI can be too narrow. Conversely, if structural uncertainty is not represented by the ensemble at all (e.g., missing extreme behaviors), the CI can also be misleadingly narrow even if correlations are addressed. Because the paper uses these intervals to support quantitative claims with 95% bounds, the statistical misinterpretation affects the credibility of the uncertainty statements central to the conclusions. The cited literature indicates that dependence and shared biases are expected, so the paper should have either modeled dependence or avoided probabilistic CI claims based purely on model spread. This evidence directly supports that the paper’s reported 95% CIs for PM\\$_{2.5}$\\ are not clearly justified.\n\nReferences:\n[1] <a id=\"ref1\"></a>[Knutti, R. et al. Challenges in combining projections from multiple climate models (2009, revised 2010; submitted to *Journal of Climate*)](https://www.image.ucar.edu/idag/Papers/knutti_tebaldi_combining_projections.pdf)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|GPT|5", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "This paper reports internally inconsistent magnitudes and confidence intervals for key driver contributions (population aging and disease mortality), which undermines the reliability of the quantitative conclusions about dominant drivers and offsets.\n\n\"Population aging is the only factor contributing to the growth of DAPP in the sustainable development (SSP1-2.6) scenario and fossil fuel development (SSP5-8.5) scenario, resulting in increases of 674 thousand and 703 thousand DAPP per annum, respectively.\"\nThis sentence assigns specific magnitudes to the aging contribution but does not reconcile them with other parts of the manuscript that report different values for the same concept and scenarios. When a paper’s core conclusion depends on the magnitude of a single driver (aging) and its ability to offset improvements, internal inconsistency makes it unclear which numbers should be trusted. Such inconsistencies also impede any attempt at external validation or re-analysis, because reviewers cannot determine the target quantities. In quantitative health impact assessment, consistent reporting of point estimates and uncertainty intervals is essential, especially when comparing scenarios and provinces. If the numbers are correct but reported inconsistently, the manuscript still fails its communication burden for scientific claims that are primarily numerical. If the inconsistencies reflect underlying calculation differences, they raise concerns about analysis integrity. Either way, the manuscript needs reconciliation to support its headline claims.\n\"Specifically, in these two scenarios, population aging brings increases of 730 thousand (718-746, 95% CI) and 634 (608-656, 95% CI) thousand DAPP, respectively. Meanwhile, disease mortality is an important factor alleviating the growth in DAPP, and more than 70% of the reduction in DAPP is due to the reduction in disease mortality which decreased DAPP by 615 (602-636, 95% CI) thousand, 658(608-656, 95%CI) thousand, 693 (678-726, 95% CI) thousand, and 636 (611-657, 95% CI) thousand\"\nWithin this single passage, the disease-mortality reduction is reported as \"658(608-656, 95%CI)\", where the lower bound exceeds the upper bound, which is not a coherent 95% interval. The same passage also gives aging-contribution magnitudes (730 and 634 thousand) that conflict with the earlier statement of 674 and 703 thousand for ostensibly the same scenarios and period. Because the decomposition results are central to the paper’s claim that aging is the leading driver and offsets improvements, contradictions in these figures directly weaken the reliability of the conclusions. In health burden studies, inconsistent or incoherent uncertainty intervals are especially problematic because they can signal coding/reporting errors or mis-specified uncertainty propagation. Even if some discrepancies are typographical, they occur in the manuscript’s main results narrative and thus materially affect interpretability. Resolving these inconsistencies is necessary before the quantitative claims can be considered robust.\n\"Overall, from 2017 to 2035, population aging will be the most important driver of DAPP growth. In the sustainable development (SSP1-2.6) and fossil fuel development (SSP5-8.5) scenarios, population aging is the only factor leading to DAPP growth in 2017-2035, resulting in increases of 718-746 (95% CI) thousand and 608-656 (95% CI) thousand DAPP, respectively.\"\nThis conclusion section reports aging-related increases as ranges matching the earlier confidence intervals, but it presents them as \"increases of 718-746\" and \"608-656\" rather than as point estimates with intervals, which is inconsistent with standard reporting elsewhere in the paper. It also conflicts with the earlier per-annum values (674 and 703 thousand) and creates ambiguity about whether the paper is referring to total change over 2017–2035 or annualized contributions. Such ambiguity is consequential because the paper’s policy implications depend on whether aging adds on the order of ~600–700 thousand deaths total or per year. Mixing units and reporting conventions can lead readers to substantially misinterpret the magnitude of the aging effect. In driver decomposition studies, it is common to report both total contributions over a period and annual rates, but this requires explicit labeling and consistent numerators/denominators. The evidence shows the manuscript does not maintain that consistency, undermining confidence in its main quantitative takeaways.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "The paper uses coarse-resolution (1° × 1°) CMIP6 data for future PM2.5 projections, which is insufficient for accurately estimating population exposure and health impacts at the provincial level in China.\n\n\"Future PM_{2.5} composition data came from the CMIP6 dataset... spatial resolution 1°\"\nA spatial resolution of 1° (approximately 110 km) is too coarse to capture the spatial heterogeneity of PM2.5 concentrations, particularly the high pollution levels in densely populated urban centers. This leads to significant exposure misclassification, as the \"population-weighted\" concentration will be biased by the smoothing effect of the coarse grid, failing to reflect the actual exposure of people living in pollution hotspots.\n\"Concentration of PM_{2.5} on surface (spatial resolution 0.1°)\"\nThe authors use high-resolution (0.1°) data for the historical period but switch to coarse (1°) data for the future period. This inconsistency introduces a methodological bias, as the future projections lose the spatial detail present in the baseline, making the comparison and trend analysis unreliable.\n\"Punger and West (2013) found that coarser resolution decreased the estimated health burden\" [1]\nPrevious literature has demonstrated that using coarse resolution models for health impact assessment can lead to significant biases (often underestimation) compared to high-resolution models. The study should have used downscaled CMIP6 data or regional climate model outputs (e.g., WRF-Chem) to ensure valid exposure estimates.\n\nReferences:\n[1] Punger, E. M., & West, J. J. (2013). The effect of grid resolution on estimates of the burden of ozone and PM2.5 on premature mortality in the USA. Air Quality, Atmosphere & Health, 6(2), 309-321. https://doi.org/10.1007/s11869-011-0133-2", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "The paper fails to clearly describe the methodology and data sources used to project future age-standardized mortality rates for specific diseases, making the results non-reproducible and the conclusions regarding the \"aging challenge\" questionable.\n\n\"Most age-standardized death rates of diseases in different scenarios demonstrated a downward trend\"\nThe paper states this trend as a result but does not explain how it was derived. Did the authors assume a continuation of historical trends, use GBD forecasts, or apply specific SSP-based health scenarios? Without explicit documentation of the projection method, it is impossible to verify whether the assumed decline in baseline mortality is realistic or consistent with the socioeconomic pathways (SSPs) used.\n\"In addition, for future disease mortality, we used the GBD development prediction model to estimate it according to the study by Foreman et al^{55}.\"\nWhile the paper cites Foreman et al. (2018), it does not explain how the national-level forecasts from that study were applied to the provincial-level baselines used in this study. Given that provincial health disparities are a key focus of the paper, simply applying a uniform national trend would be methodologically flawed, but the text provides insufficient detail to determine what was actually done.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "The paper inaccurately claims that previous studies have not considered the combined influence of multiple drivers (socioeconomic, climate, aging) on PM2.5-related deaths, ignoring existing literature that has already conducted such analyses.\n\n\"most studies mainly focus on the changes in DAPP under the influence of a single factor, which does not consider the driving effect of socioeconomic development and climate change on DAPP simultaneously.\"\nThis claim is factually incorrect. Geng et al. (2021) [2] conducted a comprehensive decomposition analysis of PM2.5-related deaths in China from 2002 to 2017, quantifying the contributions of eight factors including population aging, exposure, and baseline mortality. Similarly, other studies have projected future health burdens considering multiple drivers.\n\"we still do not have a reliable and effective estimate of DAPP that accounts for the driving factors of socioeconomic pathways and changes in climate across different provinces in China.\"\nBy failing to acknowledge and discuss these prior works, the paper overstates its novelty. The contribution should be framed as an update using CMIP6 and SSPs, rather than the \"first\" to consider multiple factors.\n\nReferences:\n[2] Geng, G., Xiao, Q., Liu, S., Liu, X., Cheng, J., Zheng, Y., ... & Zhang, Q. (2021). Drivers of PM2.5 air pollution deaths in China 2002–2017. Nature Geoscience, 14(9), 645-650. https://doi.org/10.1038/s41561-021-00792-3", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Gemini|5", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "The study relies on the Integrated Exposure-Response (IER) function (or GBD 2019 method), which may underestimate the mortality burden compared to newer Global Exposure Mortality Models (GEMM), particularly at the high concentration levels found in China.\n\n\"estimated and verified the spatiotemporal changes of DAPP in China... based on a risk assessment framework\"\nThe paper uses the GBD methodology. However, Burnett et al. (2018) [4] introduced the GEMM, which includes data from Chinese cohorts and generally estimates significantly higher mortality rates for PM2.5, especially for non-accidental causes.\n\"Although some estimates based on the GEMM model were higher than our estimates^{14}, the results showed a similar trend over time.\"\nWhile the authors acknowledge GEMM yields higher estimates, they dismiss it by claiming trends are similar. However, for a study quantifying the absolute number of deaths to assess the \"aging challenge\", the magnitude matters. A sensitivity analysis comparing IER and GEMM results would provide a more robust assessment of the potential burden.\n\nReferences:\n[4] Burnett, R., Chen, H., Szyszkowicz, M., Fann, N., Hubbell, B., Pope III, C. A., ... & Spadaro, J. V. (2018). Global estimates of mortality associated with long-term exposure to outdoor fine particulate matter. Proceedings of the National Academy of Sciences, 115(38), 9592-9597. https://doi.org/10.1073/pnas.1803222115", "reviewer_type": "ai", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|61|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "The title of the paper is slightly confusing. How about “The challenge of population aging for future mitigation of deaths attributable to PM2.5 air pollution in China”?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "I think it would be better to use “air pollution” rather than just “pollution” throughout (e.g. in the title).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "I’m not keen on creating new acronyms, such as DAPP. As far as I’m aware, this isn’t a common term used in the air pollution field (other than in past papers by the authors).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "[Abstract] It would be useful to briefly state what the scenarios represent. You might just say e.g. “scenarios representing different levels of sustainable development”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "[Abstract] The abstract is a little confusing because it first says “The results show that from 2017 to 2035, DAPP in China will decrease...”, then the next sentence says “We found that population aging will be the leading driver contributing to the increase in DAPP...”. Should the second sentence say something like “We found that population aging will be the leading driver tending to increase DAPP...”?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "[Introduction] Lines 47-51: Are these lines referring specifically to China? Or global?", "reviewer_type": "human", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|61|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "[Introduction] Lines 92-95: It might be worth emphasising here that the RCPs represent greenhouse gas concentration trajectories (as opposed to air pollutants).", "reviewer_type": "human", "label": "error", "error_type": "Neglect", "label_origin": "expert+llm-filter"}
{"id": "prb|61|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "[Introduction] Line 111: Perhaps clearer to say “…impact of population aging on DAPP in China…”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_1|9", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "[Results] Lines 161-163: I don’t understand the sentence starting “In addition, it is worth noting...”. Please can the authors clarify?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_1|10", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "[Results] Lines 182-185: I also find the sentence here confusing: “In the sustainability scenario (SSP1-2.6), ...”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_1|11", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "[Results] Lines 187-188: Like the abstract, this sentence is a little confusing because it suggests DAPP increases from 2017 to 2035.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_1|12", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "[Results] Figure 3: It would be helpful to the reader to explain briefly how to read/interpret the plots (either in the figure title or in the main text).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_1|13", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "[Discussion] Line 259: I don’t think the paper by Wang et al was mentioned in the Introduction when making the case for the research. Can the authors explain how their study compares (and improves upon) the Wang et al study?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_1|14", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "[Discussion] Lines 272-286: The start of the paragraph suggests that “two aspects” will be discussed but the paragraph seems to make three distinct points (\"Third, with the fast-growing aging population in China, ...\").", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_1|15", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "[Discussion] Lines 289-292: The KAYA model needs a little further brief description and a reference. What does it do?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_1|16", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "[Discussion] Lines 318-339: I’m not entirely sure what point is being made in this paragraph and what it adds to the paper. Is the paragraph needed? Or could it perhaps be made shorter?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_1|17", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "[Discussion] Lines 349-360: These recommendations (especially regarding pensions) seem a little outside the scope of the research and do not directly follow from the main findings on air pollution. Can you more directly link the paragraph to your findings?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_1|19", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "[Materials and Methods] Lines 439-442. More detail would be helpful on how CMIP6 estimates PM2.5 levels, since this is central to the study.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_1|20", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "[Materials and Methods] Lines 478-488: Do the inputs described here all come from CMIP6? Can you comment on the basis for the formula from Chowdhury et al and Van Donkelaar et al?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "[Presentation of the results] I would suggest the authors to provide, very briefly, additional information on the method and data used before the presentation of the results. In particular, it is difficult to understand the meaning of the different drivers with no prior explanation on the nature or how these are defined in the analysis. For example, how the authors disentangled the contribution of population growth from aging (changes in population structure)? I believe it would be also beneficial to clarify what each driver means.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "[Results on the drivers] I personally see that Figure 3 is not very clear. I wonder if it would be better to just report in bars the contribution of each (over the same x axis) for each time point.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "[Results on the drivers] The explanation of the findings is not clear either: for example, the authors start saying that the main contributor to the increase in DAPP is aging, but in the previous section they mentioned that DAPP decreases or remains similar in all scenarios. In the discussion this statement is even more prominent - \"Our study found that population aging will be the primary factor driving an increase in DAPP from 2017-2035\". In my opinion, this is not accurate, and probably a more appropriate way to formulate this statement would be that ageing would attenuate the benefits of mitigation strategies by reducing or counteracting the decrease in DAPP. I understand that the addition of the other components will give a decreasing pattern, but I am sure the authors can find another way to describe the findings.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "[Results on the drivers] Figure 6: although I could find it useful, it is a bit too complex and I would probably try either to simplify or provide more information in the same figure and the legend.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "[Results on the drivers] I would suggest moving Figure 4 into suppl file.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "Why the authors use specific years to report the findings, instead of time intervals (e.g., 5-year interval)? this approach would smooth out the influence of abrupt changes due to data artifacts.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "Limitations of the study: the authors do not discuss potential limitations of their study. For example, the use of constant association estimates (is it possible that in the future pop would reduce their vulnerability to PM2.5?)", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "In Figure 5 authors report the contribution of older pop in DAPP for each cause, but they do not report the actual change in DAPP for each cause (or it was not evident to me).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "Introduction: Paragraph starting in line 66: when the authors describe the existing papers, it would be useful to provide an overview of the findings in previous assessments.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_2|10", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "It is important to highlight that \"elderly\" is currently not used - better older population or older adults.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_2|11", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "Figure 2: the size of the bars is so small that it is very difficult to see it in the printed version. I would suggest changing the format or removing it (maybe include a table in suppl file).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "Starting with the abstract I think the language and the results should be presented with more details, for instance, the results presented with a variation of 31.9 and 178.8 in the DAPP could be better related to the scenarios. There are three scenarios presented, from less radiative impact to the highest impact scenario, how they are related to the findings. The numbers don't seem consistent with the results presented in the results section.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "In the introduction, the first sentence should be contextualized. The authors wrote that “The air pollution by PM2.5 has increased”, but this happens at some locations. The PM2.5 concentrations at different places are only above the new air quality guidelines from WHO.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "As the subject of the manuscript is related to the aging of population, it would be adequate to include references on the health effect of PM2.5 on the elderly. There are references of studies around the world discussing the impact of pollution on the elderly.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "The sentence “d climate change (e.g., transformation and diffusion of air pollution)” is not clear. Which climate change parameters will affect the diffusion of air pollution. It is too vague.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "[Methods] Which are the driving factors considered? They are presented in the supplementary material but the decomposition of the factors could be discussed in the results.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "[Methods] In line 202 and even before the authors discussed the decreasing trend in the disease mortality (what is really expected), but could this be outshined by the aging of the elderly population?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_3|7", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "[Methods] In my view a discussion about the meteorological conditions in the scenarios and their synergic effects should be presented. The scenarios indicate the increase in the number, duration and intensity of the heat waves, how will these conditions affect the elderly population? This is not pertinente to be discussed?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_3|8", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "[Methods] My last comment is related to the legends of the figures. They need to be improved, not all the information to understand them are presented.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_3|9", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "[Methods] For instance Figure 3 presents the different factors to DAPP changes, but DAPP is one of the variables presented with the other factors. I think it is not clear what is being presented.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_3|10", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "[Methods] In the discussion the model KAYA needs a reference.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|61|Human_3|11", "source": "prb", "split": "test", "paper_id": "prb61", "comment": "[Methods] Also the recommendation to activities indoors when there are high levels of pollutants can not work if the indoors ambients are contaminated with high levels of pollutants, as occurs with the use of solid fuels for cooking, for instance.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Claude|1", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "The paper claims to demonstrate a method for \"single-activity resolved fiber photometry\" that enables \"single-source temporal activity resolution,\" but all experimental validations are performed ex vivo (fluorescent beads and fixed brain slices) with artificial DMD-generated temporal profiles, rather than in actual living mice with real neuronal calcium transients.\n\n\"Here, we demonstrate how to separate the time trace signals of several fluorescent sources probed by a thin (≈ 200 µm) MMF with typical implantable length in a mouse brain.\"\nThis statement from the abstract implies the method has been demonstrated for physiological conditions, but all experiments in the paper use simplified phantoms (fluorescent beads) and fixed tissue samples rather than living brain tissue. The \"validation\" mentioned in Section 2.2 uses a 50 µm fixed brain slice where neurons are structurally labeled (Gad-eGFP), but activity is simulated via DMD excitation patterns rather than actual calcium transients from living neurons.\n\"Besides, we validated our approach in a more realistic condition by selectively exciting a few structurally Gad-eGFP labeled neurons in a 50 µm fixed brain slice with literature-available time traces to mimic neuronal activity.\"\nThe validation uses artificially imposed temporal patterns on static tissue rather than actual calcium transients. Real in vivo neuronal calcium dynamics exhibit complex, stochastic patterns with variable event shapes, amplitudes, and temporal structures that differ substantially from the controlled DMD-generated traces used here. Standard practice in calcium imaging method validation involves either simultaneous electrophysiological recordings or actual in vivo imaging data ([Pnevmatikakis et al., Neuron, 2016][1]; [Theis et al., 2016][2]).\n\"We finally suggest that this method could be applied in vivo in freely behaving animals by coupling the short implanted fiber with a miniscope (MiniDART concept).\"\nThe MiniDART concept remains speculative. While the paper demonstrates that a miniscope can detect patterns from a single fluorescent bead (Fig. 4), no actual demixing of multiple sources using the miniscope is shown, and no in vivo neural activity is measured. The gap between proof-of-principle with beads/fixed tissue and functional in vivo application remains substantial and unaddressed experimentally.\n\nReferences:\n[1] [Pnevmatikakis, E.A., et al. \"Simultaneous Denoising, Deconvolution, and Demixing of Calcium Imaging Data.\" Neuron 89(2):285-299 (2016)](https://pmc.ncbi.nlm.nih.gov/articles/PMC4881387/)\n[2] [Theis, L., et al. \"Benchmarking spike rate inference in population calcium imaging.\" Neuron 90(3):471-482 (2016)](https://pmc.ncbi.nlm.nih.gov/articles/PMC4888799/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Claude|2", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "The NMF algorithm requires manual specification of the number of components (rank), which must approximately match the number of fluorescent sources. The paper does not provide a validated automatic method for determining this parameter, making the approach impractical for real experimental conditions where the number of active neurons within the fiber's field of view is unknown.\n\n\"The parameter n_components (which is the chosen NMF rank) changes depending on the experiment and a more detailed discussion about how to choose this value can be found in the supp info. In particular, the rank used in Fig. 02 was rank Fig2 =9 (explained in the supp info), and the rank for Fig. 03 was rank Fig3 = 5.\"\nThe authors manually set different rank values for different experiments based on prior knowledge of the sample (6 beads requiring rank=9, 4 neurons requiring rank=5). In real in vivo fiber photometry applications, the number of neurons within the fiber's field of view contributing to the signal would be unknown and potentially variable over time. Without an automatic rank determination procedure, the method requires user intervention that may not be feasible.\n\"Thus, counting the maximum number of unique patterns demixed by NMF could be a way to count the real number of sources probed by the fiber. A more technical analysis of it can be found in the supp info.\"\nThis proposed approach for estimating the number of sources is vague and not rigorously validated in the main text. This is a well-known limitation of NMF-based methods. As noted in the CaImAn pipeline paper: \"A common limitation of matrix factorization algorithms is that the number of components that the algorithm seeks during its initialization must be pre-determined by the user\" ([Giovannucci et al., eLife, 2019][3]).\n* Quote from literature: \"For example, Pnevmatikakis et al. (2016) suggest detecting a large number of components which are then ordered according to their size and activity pattern, with the user deciding on a cut-off threshold.\" ([Giovannucci et al., eLife, 2019][3])\nMore sophisticated calcium imaging analysis pipelines like CaImAn address the rank selection problem through automated quality assessment tests based on unsupervised and supervised learning. The method presented in this paper does not incorporate such approaches and relies on user-specified parameters, which limits its practical applicability.\n\nReferences:\n[3] [Giovannucci, A., et al. \"CaImAn an open source tool for scalable calcium imaging data analysis.\" eLife 8:e38173 (2019)](https://elifesciences.org/articles/38173)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Claude|3", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "The paper assumes that \"scattering fingerprint\" patterns from the multimode fiber remain stable and uniquely identifiable over time, but this critical assumption is not experimentally validated under any perturbation conditions relevant to in vivo applications (such as fiber micro-bending, tissue movements, or temperature changes).\n\n\"Here, we call these short MMF patterns as scattering fingerprints.\"\nThe term \"fingerprints\" implies stable, unique identifiers for each source. However, all experiments were conducted under highly controlled static conditions where neither the fiber nor the sample moved. No experiments tested whether these patterns remain stable under perturbations that would occur in living animals.\n\"Typically, even long fibers have critical ~6 mm bending radius (with typical bending stress of ~700 MPa), where the Young modulus of multimode fibers changes very little (less than 1%) and its value is for practical purposes considered constant. Therefore, short fibers as the ones we used (~8 mm long) are significantly rigid and very difficult to be bent.\"\nWhile the paper argues theoretically that short fibers are rigid, no experimental evidence demonstrates that the scattering patterns are stable under any mechanical perturbation. The transmission matrix of multimode fibers is known to be sensitive to bending and environmental changes. Prior work has shown that even small fiber perturbations can affect speckle patterns significantly ([Li et al., Light: Science & Applications, 2021][4]; [Ohayon et al., Biomedical Optics Express, 2018][5]).\n* Quote from literature: \"However, as well described in wavefront shaping experiments, speckle wavefronts are extremely sensitive to fiber bending, torsion movements, and temperature changes along the fiber\" (from the paper itself)\nThe authors acknowledge this sensitivity for long fibers but assume without experimental verification that short fibers are immune to such effects. Even if the fiber is rigid, brain tissue pulsations, blood flow, and animal movements could cause relative motion between the fiber tip and the neural sources, potentially altering the observed patterns in ways not characterized in this study.\n\nReferences:\n[4] [Li, S., et al. \"Compressively sampling the optical transmission matrix of a multimode fibre.\" Light: Science & Applications 10, 88 (2021)](https://www.nature.com/articles/s41377-021-00514-9)\n[5] [Ohayon, S., et al. \"Minimally invasive multimode optical fiber microendoscope for deep brain fluorescence imaging.\" Biomedical Optics Express 9(4):1492-1509 (2018)](https://pmc.ncbi.nlm.nih.gov/articles/PMC5905901/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Claude|4", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "The paper presents results from only single experiments per condition (one 6-bead phantom, one 4-neuron fixed brain slice), with no repeated trials or statistical analysis across multiple experimental instances to establish reproducibility or generalizability.\n\n\"More specifically, we obtained an average value of < δg,n > = δavg = 85.4% with a standard deviation of std = 3.6% (Fig. 02 g).\"\nThe \"average\" and \"standard deviation\" reported are computed across the 5 successfully demixed beads within a single experiment, not across multiple independent experimental replicates. This provides no information about reproducibility across different fiber preparations, different bead arrangements, or different days. The failure of bead #6 (located at the edge) is mentioned but not systematically characterized.\n\"As in the previous experiment, the GT-NMF temporal trace correlation values obtained were high, with an average value of < δg,n> > = δavg = 86.7%, and a standard deviation of std = 2.8%.\"\nSimilarly, this result from the brain slice experiment (Fig. 3) represents a single experimental instance with only 4 neurons. Standard validation protocols in calcium imaging analysis typically involve testing on multiple datasets with ground truth, as demonstrated in benchmark studies ([Theis et al., Neuron, 2016][2]; [Giovannucci et al., eLife, 2019][3]). Without repeated experiments, it is impossible to assess the robustness of the method to variations in sample preparation, fiber alignment, or imaging conditions.\n\"However, the NMF algorithm could not reliably recover the time trace and fluorescence patterns corresponding to bead #6 due to low SNR, probably because it was localized too far from the center\"\nThe failure mode for bead #6 suggests spatial position within the fiber field of view affects demixing success. However, no systematic characterization of how demixing performance varies with source position, intensity, or temporal correlation between sources is provided. A single experiment cannot establish the boundaries of method applicability.\n\nReferences:\n[2] [Theis, L., et al. \"Benchmarking spike rate inference in population calcium imaging.\" Neuron 90(3):471-482 (2016)](https://pmc.ncbi.nlm.nih.gov/articles/PMC4888799/)\n[3] [Giovannucci, A., et al. \"CaImAn an open source tool for scalable calcium imaging data analysis.\" eLife 8:e38173 (2019)](https://elifesciences.org/articles/38173)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|GPT|1", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "The manuscript makes an insufficiently supported claim (Validity, Conclusions) that its unconstrained NMF demixing on raw multimode-fiber camera videos can be used as a calibration-free approach for implantable-length fibers in freely behaving animals, because it does not test the core failure mode for such settings—time-varying fiber perturbations that change the spatial fingerprints—while still extrapolating to “freely-behaving” and “long-term freely-moving” use cases.\n\nFurthermore, we show that commercial and low-cost open-source miniscopes display enough sensitivity to image the same fluorescence patterns seen in our proof of principle experiment, suggesting that a whole new avenue for novel minimally invasive deep brain studies with multimode fibers in freely-behaving mice is possible.\nThis sentence explicitly extends the paper’s proof-of-principle to a “freely-behaving mice” application, which is a materially harder regime than the demonstrated benchtop bead and fixed-slice experiments. In freely behaving settings, relative motion (animal motion, cable tugging, headcap forces) introduces fiber bending/torsion/temperature fluctuations, which can change the mapping between distal sources and proximal patterns over time. The proposed demixing assumes that each source has a consistent spatial fingerprint whose intensity “fluctuates accordingly” with the temporal trace, so time-variation of fingerprints directly threatens identifiability. The manuscript does not present experiments where the fiber is perturbed during acquisition and demixing is evaluated under that perturbation. Without that evidence, the application-level conclusion is not robust and may not hold outside the controlled lab alignment used here.\nWith this approach, we show that it is possible to extract single-source time traces in fiber photometry without the need to perform any complicated calibration procedure.\nThis sentence claims that the method avoids calibration, positioning it against transmission-matrix/wavefront-shaping approaches that require repeated characterization. However, “no calibration” is only meaningful if the spatio-temporal fingerprints remain stable enough during the recording for a fixed factorization to separate sources reliably. The paper’s validation uses ground-truth controlled excitation in static conditions, which does not probe the stability assumptions under realistic perturbations. In practice, if the forward mapping drifts, the NMF factors (spatial components) change over time, and an unconstrained static NMF can misattribute temporal activity to incorrect components. Because the manuscript does not quantify stability or present a strategy for handling time-varying mixing, the calibration-free claim is not adequately substantiated for the target use case.\nThis new way of measuring individual fluorescence time traces from an ensemble of fluctuating sources profits from the short length of multimode fibers that are naturally more rigid (bending resistant) and therefore very suitable to be used in long-term freely-moving mice neuroscience experiments.\nThe conclusion here depends on an untested physical premise (“naturally more rigid (bending resistant)”) being sufficient to ensure stable fingerprints over the full duration of “long-term” experiments. Even if short fibers are more rigid than long fibers, small perturbations can still occur (e.g., micromotion at the skull interface, coupling changes, temperature drift), and these can matter for speckle-like or structured scattering patterns. The manuscript does not measure or bound fingerprint drift as a function of bending radius, torsion, or time, nor does it evaluate demixing accuracy as these perturbations occur. The paper’s own narrative sets stability as the key differentiator versus long-fiber TM methods, so empirical stability characterization is central rather than optional. Without perturbation tests, the “very suitable” claim remains speculative.\nUnfortunately, bending, stressing, or changing the temperature of the fibre changes this matrix, which traditionally then requires a time-consuming re-calibration.\nThis statement from Hu et al. highlights that multimode-fiber transmission behavior is sensitive to common perturbations, framing calibration/stability as a central experimental challenge for fiber-based imaging. The reviewed manuscript’s primary advantage claim is that it can demix without such calibration and can be used in freely moving animals. The contradiction is not that NMF demixing is impossible, but that the key practical impediment is time-varying mixing induced by perturbations—exactly the kind of variability that breaks static factor models. Because the manuscript does not test demixing under bending/torsion/temperature drift, it does not demonstrate that its approach escapes the need for re-characterization in realistic conditions. This undermines the validity of the paper’s applicability claims beyond the static benchtop demonstrations. ([4](#ref4))\nHowever, as well described in wavefront shaping experiments, speckle wavefronts are extremely sensitive to fiber bending, torsion movements, and temperature changes along the fiber, which demands a long and meticulous wavefront propagation characterization (e.g., calibration using spatial light modulators, SLM) to compensate for all the changes in spatial properties of the speckles.\nThe manuscript itself correctly identifies bending/torsion/temperature sensitivity as a decisive difficulty for multimode-fiber imaging approaches. The paper then argues that short fibers are “more stable” and therefore pragmatic for freely behaving experiments, but it does not empirically validate that short-fiber fingerprints are stable enough under realistic motion. Importantly, the proposed demixing still uses spatial fingerprints as identifiers, so any change in the fingerprint morphology can cause component mismatch even if the patterns are not “fully evolved speckle.” A robust claim would require either (i) explicit perturbation experiments demonstrating stable demixing despite motion, or (ii) an algorithmic extension for time-varying factors. The absence of such evidence makes the extrapolation to freely behaving settings methodologically premature.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|GPT|2", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "The manuscript’s central conclusion (Conclusions, Appropriate use of statistics and treatment of uncertainties) that it “retrieves” individual source activity is not demonstrated with a sufficiently rigorous evaluation, because it reports primarily within-experiment correlation summaries (and qualitative figure comparisons) without independent repeats, without full cross-talk/false-discovery characterization, and while showing at least one clear failure case (low-SNR edge source) that is not systematically analyzed.\n\nMore specifically, we obtained an average value of < δ<sub>g,n</sub> > = δ<sub>avg</sub> = 85.4% with a standard deviation of std = 3.6% (Fig. 02 g). However, the NMF algorithm could not reliably recover the time trace and fluorescence patterns corresponding to bead #6 due to low SNR, probably because it was localized too far from the center, i.e. at the edge of the field of view (fiber core border, see Fig. 02 c), as suggested by the low intensity of GT scattering pattern (Fig. 02 d, index 6).\nThis passage shows that the main quantitative metric reported is a correlation coefficient averaged across sources within a single controlled experiment, and that one of six sources fails to be recovered. An average correlation is not, by itself, sufficient to establish demixing fidelity because it does not quantify cross-talk (activity leakage from other sources), false positives (spurious components), or amplitude/kinetics distortion relevant for calcium dynamics. The failure of bead #6 indicates a sensitivity cliff with respect to SNR and field position, yet the paper does not map recovery quality as a function of SNR, background, overlap, or distance from the core axis. Without such characterization, it is unclear how often similar failures would occur in biological settings where sources differ widely in brightness and background varies over time. The conclusions about “single-source temporal activity resolution” therefore exceed what the presented evaluation supports.\nAs in the previous experiment, the GT-NMF temporal trace correlation values obtained were high, with an average value of < δ<sub>g,n</sub>���> = δ<sub>avg</sub> = 86.7%, and a standard deviation of std = 2.8%.\nThe fixed-slice validation is again summarized primarily through an average correlation statistic, but the manuscript does not report how many neurons/sources were analyzed across how many independent trials (fields of view, slices, or animals). The Methods section specifies “data from one GAD65-EGFP transgenic mouse,” which suggests limited biological replication and therefore limited generalizability of the reported statistics. Moreover, correlation does not assess whether inferred traces preserve spike timing or transient kinetics, which is crucial for neuroscience use cases. Because the validation uses “literature-available time traces” injected via DMD-like excitation, it is not equivalent to recovering spontaneous in vivo activity with motion and neuropil/background confounds. The lack of uncertainty quantification across independent experimental repeats weakens the robustness of the paper’s performance claims.\nThe NMF parameters chosen ignored the additional parametric terms that are introduced to account for the sparsity of the data.\nThis sentence makes clear that the analysis intentionally uses an unconstrained formulation (no sparsity/priors) despite the paper’s own acknowledgment that constraints can improve NMF for calcium-like signals. In calcium imaging, accurate demixing in the presence of background and overlap typically leverages structured priors (spatial locality, temporal dynamics, background models). Using an unconstrained model increases the risk of component splitting/merging and of fitting background fluctuations as sources, which should be evaluated explicitly. Yet the manuscript’s reported metrics do not include systematic checks for component stability across initializations, residual analysis, or validation under varying background levels. This mismatch between model choice and evaluation depth makes the concluding claims about robust demixing less credible.\nOur goal is to simultaneously identify the locations of the neurons, demix spatially overlapping components, and denoise and deconvolve the spiking activity from the slow dynamics of the calcium indicator.\nThis abstract sentence from Pnevmatikakis et al. articulates a widely adopted evaluation target in calcium imaging: demixing must be paired with denoising/deconvolution and is explicitly designed for overlapping components and indicator kinetics. The reviewed manuscript’s evaluation largely stops at correlation with ground-truth excitation traces, without demonstrating robustness to overlapping sources plus fluctuating background in a way comparable to established pipelines. Importantly, the cited CNMF framework is presented and validated across multiple data modalities, including in vivo recordings, which is the regime the reviewed paper aspires to. This comparison highlights that common practice is to validate demixing methods against realistic confounds and to report more than simple correlation summaries. The reviewed manuscript’s limited quantitative evaluation leaves a gap between demonstrated capability and claimed neuroscience utility. ([1](#ref1))\nHowever, it is computationally challenging to extract single-neuronal activity from microendoscopic data, because of the very large background fluctuations and high spatial overlaps intrinsic to this recording modality. Here, we describe a new constrained matrix factorization approach to accurately separate the background and then demix and denoise the neuronal signals of interest.\nZhou et al. emphasize that microendoscopic recordings are dominated by background fluctuations and spatial overlap—two confounds also relevant to the manuscript’s intended in vivo fiber-photometry-like applications. The reviewed manuscript acknowledges that “a real GFP-labeled brain would display higher background,” but it does not present a dedicated background model or show performance under systematically varied background regimes. Because their method uses unconstrained NMF “directly on the raw data,” it is unclear how it avoids attributing background fluctuations to spurious components when applied to in vivo recordings. Established approaches explicitly model and separate background before or during demixing, and they evaluate resulting improvements quantitatively. This contrast suggests the manuscript’s performance evidence is incomplete for the conclusion that it will work reliably in realistic biological recordings. ([2](#ref2))", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|GPT|3", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "The manuscript’s methodological claim (Validity, Data and methodology) that one can “count” sources and recover their individual traces via unconstrained NMF is not operationally supported, because the method critically depends on selecting the NMF rank and matching components—steps that the manuscript tunes using ground truth or supplementary heuristics and that are known to be nontrivial and non-identifiable in non-convex NMF.\n\nIn the analysis process, the input rank of NMF determines the number of components the algorithm demixes the spatio-temporal signal. When we choose an NMF’s rank value higher than the real number of fluorescence sources, we obtain replicas of the scattering fingerprints and the background (see supp info), similar to what happened in a previous work<sup>48</sup>. Thus, counting the maximum number of unique patterns demixed by NMF could be a way to count the real number of sources probed by the fiber.\nThis passage concedes that overestimating rank yields “replicas” and background components, which is a major identifiability issue for any proposed source-counting procedure. The proposed fix—“counting the maximum number of unique patterns”—is not defined algorithmically (e.g., what similarity metric, threshold, or stability criterion defines “unique”), and it is not validated in conditions where the true number of sources is unknown. In practice, NMF can split one source into multiple components or merge multiple sources into one component depending on rank, initialization, and noise, so “unique pattern counting” can be unstable. Because the paper’s intended application is precisely the case without ground truth, the lack of a principled, reproducible rank-selection and uniqueness-testing protocol directly affects the method’s validity. The manuscript therefore does not establish that it can reliably infer the number of sources or their traces in the real deployment scenario.\nIn particular, the rank used in Fig. 02 was rank Fig2 =9 (explained in the supp info), and the rank for Fig. 03 was rank Fig3 = 5.\nThese ranks are presented as chosen per experiment and deferred to the supplementary information, which means the core determinant of the method’s output is not fully specified in the main text. Notably, Fig. 02 is described as involving “6 fluorescent bead sources,” yet the rank is set to 9, implying additional components beyond the true sources (background/replicas) are being modeled. This creates ambiguity about what constitutes a “recovered source” versus an artifact component, and how the reported correlation statistics treat such components. Without a transparent and validated rank-selection criterion, independent researchers cannot reproduce the reported results or apply the method reliably to new data. This undermines methodological transparency and the credibility of the claim that source counting is feasible.\n```python\n#load ground truth (GT)\nfgt = sio.loadmat(GT_data_str)\nact_gt = fgt['pat'].T \nnumbeads = act_gt.shape[1] #get real number of beads (from ground truth)\n\n# Here the analysis will be different depending on the expected rank:\nif make_rank_sameas_numbeads is True:\n    if add_BGD_to_rank is True:\n        rank = numbeads + 1      #set rank as number of beads + background\n    else:\n        rank = numbeads          #set rank = exact number of sources\n```\nThe provided analysis code operationalizes rank selection using the ground-truth trace matrix to compute `numbeads`, and then sets `rank` equal to `numbeads` (optionally plus background). This is valid for controlled demonstrations, but it is not available in the intended fiber-photometry use case where the number of neuronal sources is unknown and must be inferred from the mixed recording itself. It also means that at least one critical hyperparameter in the pipeline is tuned with privileged information, which can substantially inflate apparent performance when compared to real deployment. The code therefore does not implement the paper’s proposed ground-truth-free “counting unique patterns” procedure, and it does not show how rank would be chosen in vivo. This gap between claimed method and executable method is a significant reproducibility and validity issue.\nThe choice of the factorization rank $r$, that is, the problem of order model selection, is usually rather tricky. Several popular approaches are: trial and error (that is, try different values of $r$ and pick the one performing best for the application at hand), estimation using the SVD (that is, look at the decay of the singular values of the input data matrix), and the use of experts insights.\nGillis explicitly characterizes rank selection as “rather tricky,” and lists heuristic approaches like trial-and-error and SVD-based inspection—highlighting that rank selection is not a solved or trivial step in generic NMF. The reviewed manuscript’s rank choice is described as experiment-dependent and largely deferred to supplementary discussion, and the provided code uses ground truth to set rank in the proof-of-principle analysis. In the absence of ground truth, the method needs a principled selection rule and a demonstration that the inferred sources are stable under reasonable perturbations (initializations, noise, pre-processing choices). Without such a protocol, conclusions about counting sources and reliably demixing their traces remain fragile. This literature quote supports that the paper’s current treatment of rank is insufficient for a deployable method. ([3](#ref3))\nDue to the underlying non-convexity of NMF, the different solvers may converge to different minima, even when optimizing the same distance function.\nThis scikit-learn documentation statement directly underscores a practical consequence of NMF non-convexity: solutions (and therefore inferred “sources”) can vary with solver/initialization even on the same data. The reviewed manuscript does not report any stability analysis across multiple initializations, solvers, or random seeds, yet it proposes using the number of “unique patterns” to count sources. If multiple minima yield different decompositions, then the set of “unique patterns” is not well-defined unless stability is enforced and demonstrated. This matters for validity because source counting and trace attribution are only meaningful if the decomposition is consistent and robust. The documentation thus supports the criticism that the manuscript’s rank-based counting proposal needs stronger methodological safeguards and reporting. ([5](#ref5))\n\nReferences:\n[1] <a id=\"ref1\"></a> [Pnevmatikakis et al., “Simultaneous Denoising, Deconvolution, and Demixing of Calcium Imaging Data.” Neuron (2016). DOI: 10.1016/j.neuron.2015.11.037](https://doi.org/10.1016/j.neuron.2015.11.037)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|GPT|4", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "The manuscript does not meet common reproducibility expectations (Data and methodology) because the shared code depends on external, non-included `.mat` datasets and manual path editing, and parts of the codebase reference inputs/functions that are not provided in the shared materials, preventing an independent reader from reproducing the key figures and quantitative claims from the package as given.\n\nThe proof of principle setup is visually illustrated and fully described in the supp info.\nThis statement indicates that essential experimental details required to reproduce the acquisition (optical layout, timings, calibration choices, acquisition settings) are not fully contained in the main manuscript. While supplementary materials are standard, reproducibility depends on those materials being complete and accessible alongside the code and data. Here, the analysis code expects specific `.mat` file structures and frame organization (e.g., ground-truth frames included at the start of the video), which must be precisely documented to rerun the pipeline. If the supplementary information is the only place that fully specifies the setup and data formatting, then the reproducibility of the reported results hinges on that external document. The manuscript itself does not provide a self-contained specification of the data format and acquisition protocol sufficient to regenerate the same inputs. This is a substantial obstacle for independent verification.\n- Input files: *(i) raw_ensemble_video_data.mat ; (ii) ground_truth_patterns_traces_gt.mat ; (iii) NMF_demixing__Sample_Strings.py ; (iv) tools_NMF.py .*\nThe README explicitly lists `.mat` input files as required dependencies for reproducing the analysis. However, the provided materials in the preprint package do not include these `.mat` files, which means the analysis cannot be rerun out-of-the-box. Moreover, the README indicates that the user must manually configure file locations via a separate “Sample Strings” module, which makes the pipeline brittle and complicates verification. Reproducibility in computational imaging papers typically requires either distributing the data (or a stable download link) and providing a one-command script/notebook that executes end-to-end. In the absence of the stated inputs, independent readers cannot reproduce the figures or validate the correlation statistics.\n```python\n# Here use your data path. example (Windows):\ndata_root_path = 'C:\\\\_RIMOLI_\\\\'     ### folder root path (string)\ndata_folder = '__data__\\\\20221109'   ### folder name (string) of the folder that contains the data (.mat files)\ndata_name =  'data_09112022_001' ### filename (string) of .mat file\n```\nThis configuration hard-codes a machine-specific Windows path and a particular dataset name, requiring manual modification before the code can run in a new environment. More importantly, it presupposes that the user already has the underlying `.mat` data organized in a specific folder structure, but the manuscript package does not include those files nor a documented fetch procedure for them. This means the code is not a complete computational artifact: it is a template that depends on unavailable external data. Such a setup prevents straightforward reproduction of the main claims by reviewers or readers, especially when combined with the paper’s reliance on ground-truth-specific frame ordering. This is a significant reproducibility gap for a methods paper.\n```python\n#load ground truth\nfgt = sio.loadmat('data_09112022_001_gt.mat')\nact_gt = fgt['pat'].T\n#normalize ground truth traces (for doing comparisons later)\nact_gt_norm = tNMF.norm_dimension(act_gt, dim = 1, mode='0to1')\n#load dataset\nf = h5py.File('data_09112022_001.mat', mode = 'r')\nvideo = np.array(f['video_data'])\n```\nThis example script assumes local presence of specific `.mat` filenames and therefore cannot run without the unpublished data files. Additionally, it calls `tNMF.norm_dimension(...)`, but the provided `tools_NMF.py` in this package (as shared) does not define `norm_dimension`, implying the example is not directly executable even if data were present. For a reproducibility package, example scripts should execute successfully with provided dependencies or clearly specify missing modules and how to obtain them. Because the analysis code is central to the paper’s quantitative claims, non-executable example code undermines confidence that the reported results can be independently verified. This is not a cosmetic issue: it blocks third parties from reproducing the central demixing results.\n```python\ndef iseven(number):\n    '''\n    Should be pretty easy to see what this does\n\n    Parameters\n    ----------\n    number : input number\n    Returns\n    -------\n    True/False if the number is even/odd\n\n    '''    \n    return number % 2 == 0\n\ndef isodd(number):\n    '''\n    Should be pretty easy to see what this does\n\n    Parameters\n    ----------\n    number : input number\n    Returns\n    -------\n    True/False if the number is odd/even\n\n    '''    \n    return number % 2 != 0\n```\nThis excerpt illustrates that `tools_NMF.py` ends with utility functions and (in the shared version) does not include the `norm_dimension` routine that is invoked by `NMF_example.py`. The mismatch indicates either missing code or a version inconsistency between the example and the utilities module. Version inconsistencies are particularly damaging in computational method papers because they lead to silent divergences in preprocessing, normalization, and evaluation—steps that can materially affect reported correlation statistics. Even if the proof-of-principle script avoids this function call, the repository’s presence of a non-running example script reduces confidence that the shared codebase corresponds exactly to the analyses reported in the manuscript. Independent reproduction requires the shared code to be internally consistent and complete.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "The paper claims applicability to freely behaving mice, but fails to address the critical issue of fiber bending, which changes the transmission matrix and invalidates the static NMF assumption.\n\n\"suggesting that a whole new avenue for novel minimally invasive deep brain studies with multimode fibers in freely-behaving mice is possible.\"\nThe authors explicitly claim that their method enables studies in freely behaving mice. However, this application involves significant movement of the fiber.\n\"Ideally taking into account TM changes whenever the MMF fiber is bending or changing its transmission properties during an experiment, as well discussed in previous research\"\nThe authors acknowledge in the introduction that fiber bending changes the transmission matrix (TM). However, they do not address this in their method or experiments.\n\"In the present work, we designed a proof of principle experiment (Fig. 01) ... using phantom samples made of 10 µm diameter fluorescent beads ... validation of the method while probing GFP-labelled neurons in a 50 µm thick fixed brain slice\"\nThe experiments are conducted on fixed samples with a fixed fiber. There is no data showing the method works when the fiber is moving or bending, which is the defining characteristic of \"freely-behaving\" experiments.\n\"Besides, inevitable bending and twisting of the MMF also causes strong mode couplings, which further complicates output patterns. As a result, speckle patterns at the distal end are sensitive to fiber perturbation.\" [1]\nLiterature confirms that even slight bending or twisting of a multimode fiber changes the speckle pattern (transmission matrix). NMF assumes that the spatial components (speckle patterns) are constant over time ($V \\approx WH$). If the fiber bends, $W$ becomes time-dependent ($W(t)$), violating the NMF assumption and likely causing the demixing to fail. The paper's claim of applicability to freely behaving mice is thus unsupported by the evidence and contradicts known optical physics principles regarding MMF stability.\n\nReferences:\n[1] Retrieving the optical transmission matrix of a multimode fiber using the extended Kalman filter (2020) https://opg.optica.org/oe/fulltext.cfm?uri=oe-28-7-9487", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "The paper lacks a robust, automated method for determining the NMF rank (number of sources) in the absence of ground truth, which is a critical requirement for blind source separation in real experiments.\n\n\"In the analysis process, the input rank of NMF determines the number of components the algorithm demixes the spatio-temporal signal. When we choose an NMF’s rank value higher than the real number of fluorescence sources, we obtain replicas of the scattering fingerprints and the background\"\nThe authors admit that the rank must be chosen correctly, but do not provide an automated method to do so. They suggest that replicas appear if the rank is too high, but do not quantify this or provide an algorithm to detect it.\n\"if make_rank_sameas_numbeads is True: rank = numbeads\"\nIn the provided code, the rank is set manually based on the known number of beads (ground truth). In a real experiment, the number of active neurons is unknown.\n\"In real data analysis settings, the rank of NMF is an unknown and the selection of its value is a nontrivial problem.\" [2]\nLiterature emphasizes that rank selection is a non-trivial problem in NMF-based calcium imaging analysis. The paper's reliance on manual selection or ground truth knowledge limits the practical utility of the method for discovering unknown neuronal populations.\n\nReferences:\n[2] Efficient and accurate extraction of in vivo calcium signals from microendoscopic video data (2018) https://elifesciences.org/articles/28728", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "The provided code is non-functional due to missing input data files, preventing reproduction of the results and verification of the algorithm's performance.\n\n\"Input files: (i) raw_ensemble_video_data.mat ... (ii) ground_truth_patterns_traces_gt.mat\"\nThe README file lists these input files as required.\n\"fgt = sio.loadmat(GT_data_str)\"\nThe Python script attempts to load these files. However, these `.mat` files are not included in the repository. Without the data, the code cannot be executed, and the results cannot be reproduced. This violates the principle of transparency and reproducibility.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "The paper does not compare the proposed NMF method with other standard blind source separation techniques or existing fiber photometry analysis methods to demonstrate its superiority or necessity.\n\n\"We disentangled several spatio-temporal fluorescence signals by using a general unconstrained non-negative matrix factorization (NMF) algorithm directly on the raw video data.\"\nThe authors present NMF as the solution but do not compare it with other established methods such as Independent Component Analysis (ICA), Principal Component Analysis (PCA), or constrained NMF variants (CNMF-E) used in calcium imaging.\n\"Non-negative Matrix Factorization (NMF) is an especially promising DR analysis method for analyzing activity recorded in calcium imaging.\" [3]\nWhile NMF is promising, it is standard practice to benchmark new methods against existing ones to quantify improvements in signal-to-noise ratio, source separation accuracy, or computational efficiency. The absence of such comparison makes it difficult to assess the true significance of the proposed approach.\n\nReferences:\n[3] Non-Negative Matrix Factorization for Analyzing State Dependent Activity (2023) https://pmc.ncbi.nlm.nih.gov/articles/PMC10614735/", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "Line 81-86, could authors provide estimates of how many \"scattering fingerprints\" would be available for NNMF depending on the fiber length? In-vivo experiments may have a range of 5-15mm, assuming 5 mm is needed to mount in the optical system.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "1. Line 91-92, authors claims here to validate the approach with a realistic conditions. However, in my opinion, realistic conditions include:\n\n2.1 An attempt to model/mimic brain tissue scattering.\n\n2.2. An attempt to model different density of \"neuronal\" labeling (I will comment on it below).\n\n2.3. An attempt to model or at least have an estimate of how blood vessels dilation would scramble the expected steady-state patterns discovered by NNMF and would introduce additional unique NNMF patterns.\n\nTherefore, before making a claim on the p 97- 98 that the method is \"very suitable to be used in long-term freely-moving mice neuroscience experiments\", I would suggest to do several experiments.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "Proof of principle experiment in Figure 1 is nicely designed and gives the inquire opportunity to understand in-depth the advantages and the limitations of the proposed approach. First, could authors provide more details in the illustration: were excitation-emission filters used (it is important to separate strong excitation light from emission); did the camera have the objective (if so, what was the magnification) ? Please add as a schematic drawing to the Figure 1 all components.What was the LED light power per unit area for the excitation of each point source?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "I would encourage authors to assess how many point sources could be resolved at once. For this, the proof of principle experiment in Figure 1 should be repeated with the sample containing higher density of beads, the scattering of the sample can be adjusted to closer reproduce the brain tissue (for example by embedding non-fluorescent spheres of different diameters into the sample. I am not an expert in how to mimic tissue scattering, but there are papers discussing this aspect) and, finally excite different proportion of fluorescent beads (at the same time) to create partially overlapping patterns and see how well NNMF would disentangle those.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "To mimic the activity in the brain, groups of \"neurons\" (fluorescent beads) should be excited nearly simultaneously. Simultaneous excitation in the group might be difficult for NNMF, but you may give a variance in timing of approximately 5-20 ms within a group (to profit from this variance, the camera frame rate should be close to 100 fps). Groups of 1-5, 10, 15, 20, 30 sources should be excited in separate experiments . For example, for the iteration of 5 nearly simultaneously excited beads , I would use some time intervals for one 5-beads composition and another time interval for another 5-beads composition. Run NNMF and extract number of unique sources. Do next iteration with higher number of simultaneously excited beads.\n\nFrom this experiment authors will be able to estimate: 1. number of simultaneously detected sources (at some moment in time) vs the true number of excited sources and 2. overall number of NNMF detected unique sources vs the true number of overall excited sources. It would be important to know how well the approach can demix spatial modes when they overlap. Importantly, it is ok if it does not, but authors should identify and discuss this limitation in the text as it is crucial to in-vivo application. Also, if demixing large groups of neurons is not possible , the method should not be called high-throughput (standards for high-throughput are high). Same experiment can be done for samples with scattering medium and without to compare NNMF performance.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "Fig. 2-3 no reported excitation intensity per source.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "I find correlations on figure 2-3 g-h to be not informative. It is of course nice that the pattern is similar. I would find more useful to report prediction accuracy of NNMF relative to GT. For example, training the model on GT (if the source activation is binary) and predicting with the model from the unseen NNMF data.", "reviewer_type": "human", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|62|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "Line 188-194, discuss about saturation intensity is interesting. I wonder how much of the limitation that would be when you have multiple sources distributed across the fiber field-of-view?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_1|9", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "Line 214-223, for the discussion a recent paper from Pisanello lab might be useful where they also attempt to gain spatial resolution (Bianco et al. “Orthogonalization of Far-Field Detection in Tapered Optical Fibers for Depth-Selective Fiber Photometry in Brain Tissue.” APL Photonics 7, 2 (2022): 026106. https://doi.org/10.1063/5.0073594.) Their prediction accuracy along the taper length was still relatively low, probably due to the fact that imaging across many fiber modes (degrees of freedom) can deliver a lot of information?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_1|10", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "Line 219-223, the ability to identify the displacement of the fiber relative to one bead is described as some sort of advantage, but in reality cylindrical symmetry of the fiber makes it difficult to identify multiple sources placed equidistantly from the fiber center (all would contribute to one ring). How big limitation would that be?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_1|11", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "Finally, in multiple parts of the manuscript authors stress that they \"expand the capacity of fiber photometry in resolving neuronal activity\" (line 250-252 etc.) however at the moment I see little experiments supporting this statement. Majority of my suggestions for proof of concept experiment target those improvements and will guide the experimental choices for in vivo application. Ideally, I would like to suggest using miniscope-coupled to fiber approach in-vivo, where the fiber is inserted or implanted in the mouse brain above neurons expressing GCaMP calcium indicator. Authors, could record from such mouse , NNMF estimate sources, perfuse the mouse and count GCaMP-labeled cells and compare with NNMF result. Note, for such experiment better use somata-localized GCaMP, as labeled neuronal dendritic trees may essentially spread across all field-of-view. I also understand that in-vivo experiment is possible to do only in the lab dedicated to such work (this includes already obtained animal licenses and many other skills) and this lab may not be able to do that alone but only in collaboration. Therefore, I do not suggest this as a mandatory experiment, but to enhance trust and generate more interest in this approach.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_1|12", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "It would be nice to cite earlier works (one of the papers from Papadopoulos et al. and from Turtaev et al.) which achieved spatial resolution by digitally scanning the excitation light at the fiber output.\n\nPapadopoulos, Ioannis N., Salma Farahi, Christophe Moser, and Demetri Psaltis. “High-Resolution, Lensless Endoscope Based on Digital Scanning through a Multimodeoptical Fiber.” Biomedical Optics Express 4, 2 (2013): 260–70. https://doi.org/10.1364/BOE.4.000260.\n\nPapadopoulos, Ioannis N., Salma Farahi, Christophe Moser, and Demetri Psaltis. “Focusing and Scanning Light through a Multimode Optical Fiber Using Digital Phase Conjugation.” Optics Express 20, 10 (2012): 10583–90. https://doi.org/10.1364/OE.20.010583.\n\nTurtaev, Sergey, Ivo T. Leite, Tristan Altwegg-Boussac, Janelle M. P. Pakan, Nathalie L. Rochefort, and Tomáš Čižmár. “High-Fidelity Multimode Fibre-Based Endoscopy for Deep Brain in Vivo Imaging.” Light: Science & Applications 7, 1 (2018): 92. https://doi.org/10.1038/s41377-018-0094-x.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "Although I agree with the authors that changing a fiber photometry setup in something that can give single neuron resolution (essentially for free) by only adding a camera detector can be a game changer in neuroscience, my honest opinion is that the current manuscript is still far from demonstrating that. Indeed, no real biological experiment is performed, nor the reported results can be extrapolated to infer what would happen in a real in vivo experiment in the mouse brain. In my opinion, because the biology is not there, the current manuscript does not add too much to what the authors have previously demonstrated in scattering tissue (Ref 43, 44, 48), in the sense that, if demixing can be carried out through the mouse skull, then I would expect the same process to work through a multimode fiber too.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "At the same time, since biological experiments are not carried out, I would have expected a more thorough explanation (with e.g. simulations) of the observed spatial signatures in terms of modes propagating through the fiber. As far as I understood, the relationship between the position of the beads with respect to the fiber centre and the detected fluorescence patterns, should be related to the spatial modes excited by the beads. However, this is not at all explained in the manuscript. A better description of the process would make the story stronger at least from the physics point of view.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "From my point of view, the main limitation of the work is the absence of relevant experiments from which stronger conclusions on the performances of the system in real biological conditions can be inferred. The demonstration presented in Figure 03 is not sufficient, as only 4 neurons are selectively illuminated, whereas in a real case scenario, widefield illumination would excite several more neurons distributed in more planes. A more realistic scenario would at least involve a widefield illumination of the whole field of view (which can come from the fiber itself), superimposed to the variable illumination sent by the DMD to selected neurons. To simulate the neuropil fluorescence variation, the widefield illumination should also vary in intensity over time. Ideally the authors should take a raw video recorded with a 1P miniscope with widefield illumination and try to reproduce with the DMD the variation of neuropil fluorescence and that of the neurons. This would give a better estimate of the performances of the device, and it would be best carried out in the miniDART configuration, as this is one of the main novelties of the manuscript.\n\nI am aware that going for a full in vivo experiment in mice would probably take a very long time (even if one of the corresponding authors have already expertise in similar experiments).\n\nHowever, only a real biological experiment will ultimately allow one to judge on the use of the presented method. The experiment could perhaps be carried out in brain slices expressing GCaMP, or in smaller animals, such as drosophila or zebrafish. If biological experiments are out of question for this manuscript, the authors should at least provide the more relevant experiment I outlined before in the most convincing way possible. Even in that case however, I am not sure that with no biology at all, this work should be published in Nature Communications. A specialised optical journal would, in my opinion, be more appropriate.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "The next main point that I think is missing in the current version of the paper is a more thorough explanation of the spatial signatures measured at the fiber output. As far as I understood the fluorescence signatures are a result of the excitation of different modes through the fiber. Spatially resolved fiber photometry was already demonstrated through tapered fibers by the groups of M. de Vittorio and F. Pisanello, albeit in that case the variations corresponded to variations in the z axis, rather than in the xy plane. If one takes for example this reference (Bianco et al. Orthogonalization of far-field detection in tapered optical fibers for depth-selective fiber photometry in brain tissue, APL Photonics 2022), the far field fluorescence patterns recorded on a camera detector display a characteristic ring like shape as a function of the z position (which also correspond to a different xy distance from the fiber center), which reminds me of the spatial signatures measured here by Rimoli et al. However, in Bianco et al, the signatures were measured in the Fourier plane of the fiber, whereas here the authors directly look at the fiber end surface. How are the two experiments linked to one another? My impression is that the overall effect should be pretty similar. I think that the authors should at least discuss, if any, the differences with respect to what already demonstrated through a tapered fiber, from a theoretical point of view, and in terms of advantages of their methods, so that the readers can better appreciate the novelty of their configuration. If the mechanism behind the two methods is really the same, I would expect a detailed description of why the current method is better than the previous one and which problems can it solve that could not be solved with a tapered fiber.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "Related to a better explanation of the spatial signatures, theoretically, what is the maximum number of spatial signatures that the authors should be able to unmix. Or, in other words, with reference to the Supplementary figures 3-4, which is the minimal radial and angular distances that would generate sufficiently different spatial signatures?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "There is no mention in the manuscript of the z axis at the sample plane. Is the method designed to work at one particular z plane? What would happen to the spatial signatures if the authors would displace the sample in z? I think that a proper calibration of the instrument (e.g. repeating the measurements in Supp. Fig. 3-4 at different z) as a function of the focal plane would be a very good idea.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "Related to the previous point, an experiment in which different beads at different z are excited and their fluorescence unmixed would be interesting.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "Still related to the z aspect, if one increases the distance between the fiber tip and the sample, would it be possible to extend the xy field of view beyond the diameter of the fiber (with a loss in the detected signal)? It is hard to me to understand that the field of view always stays constant and equal to the fiber diameter no matter the z plane.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "The authors, contrary to their previous works, attribute all the scattering effect to the presence of the fiber and mode mixing. However, in a real experiment, in which fluorescence sources are buried at depth in scattering tissues, the fluorescence that hits the fiber tip would be also scrambled and not clearly assignable to a particular spatial location. In the extreme case of a very deep fluorescence source, the fiber tip would be hit by a speckle pattern, so that probably, many different modes of the fiber would be excited by individual neurons. Do the authors expect to be able to demix such more complex fluorescence patterns? Or in this case, two very deep neurons (that could still be excited in 1P widefield excitation) would generate very similar spatial signatures at the fiber output?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_2|10", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "In Fig 2-3 the authors show signals that they send to the beads (or neurons) to simulate neuronal activity. However, the y scale in the traces is missing. What is the typical and minimal variation of fluorescence they can detect (the so called deltaF/F)? It is not clear if the ground truth is a signal that is zero all the time (so the target is mostly not excited) and has a higher fluorescence value at certain (very short time), or if the authors allow for the resting fluorescence. In other words, neurons have typically a certain resting fluorescence, which is not zero, and sparsely increase their fluorescence value in correspondence to neuronal activity. The resting value would generate a continuous spatial signature background (similar to Fig.2a) on top of which different spatial signature would variate when more activity is present. Is this what the authors actually do in the experiment? If not, the authors should repeat the experiment by sending as ground truth raw data (not polished deltaF/F data) from 1P miniscopes.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_2|11", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "It would also be nice to see raw fluorescence videos of the experiments (e.g, of Fig 2).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_2|12", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "I believe that the current manuscript represents a nice optical story, that adds up to the previous works of the group and previous works on fiber photometry. However, I believe that the biological conclusions the authors suggest, ‘this work can open a whole new avenue for novel and affordable minimally invasive deep brain microendoscopic studies’, are not demonstrated in the current manuscript. To me, it remains completely unknown what kind of patterns would one see in a real experiment in which many neurons expressing GCaMP (or voltage indicators) at multiple planes are excited simultaneously in a wide field manner through the fiber, and if the sensitivity of the demixing algorithm will allow different neurons to be resolved. In the absence of real biological demonstrations, in my opinion, the current work does not add sufficient novelty to what already shown by the group of Gigan (and possibly the groups of de Vittorio and Pisanello on tapered fiber), to be published in Nature Communications. I would instead recommend publishing it in an optical journal.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "I believe there are two main paths to go forward:\n\n(1) remove all claims of biological feasibility as well as the suggestive but unphysiological results in sections 2.2. and 2.3. Discuss limitations in detail. Then publish a streamlined and still interesting (in my opinion) optics paper.\n\n(2) do more realistic biological work to support the claims of this being a useful tool for biology.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "At several locations the paper either explicitly claims or strongly suggests that biological applications are almost within reach, but the actual experiments don’t support this. For example, figure 4e shows a mouse with an implanted miniscope and MMF, but the data panels in this figure are about radial displacement of beads in agarose.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "Time is given in “a.u.”. Is that a typo or does this mean that recordings were not made in real time (presumably at longer exposure times)?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "It’s a clever idea to use projection of temporal patterns onto beads as a first ground-truth evaluation (section 2.1), but the added benefit of repeating this approach with a fixed slice (section 2.2) is not clear. The slice is basically being used as a projection screen.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "Similarly, the purpose of section 2.3. is not clear. It shows that data from sparse bright beads can be recorded and unmixed on a miniscope camera. Based on section 2.1 we already know that this approach works in general. Presumably the purpose of using a miniscope was to make conclusions about realistic imaging scenarios, but what new information do we actually get about realistic configurations when the samples are sparsely illuminated bright beads without background (see below)?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "The scenarios that are supposed to mimic physiological conditions are quite unrealistic and some main limitations for in vivo imaging are not discussed. Most notably, the projected and unmixed traces seem almost noise-free. Real data has plenty of noise, mostly due to shot noise from a limited number of signal and background photons, which would very likely affect the ability to unmix the signals. As far as I can tell (not stated in the Methods), the ground truth illumination focused light on the sources only, avoiding any background fluorescence. Exposure times and illumination intensities are not given. I suggest a detailed study of how signal quality is affected by fluorescence background level, camera well depth limitations and labeling sparsity. At least, this should be treated in theory or by simulations with realistic parameters, but the manuscript would further benefit from realistic practical demonstrations. For example, authors could use a real miniscope video recording (published or recorded by the authors), tune light intensity to realistic levels and project it onto the input face of the MMF, while trying to unmix the signals on the other end.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_3|7", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "The robustness of the approach against movement of the sample and against bending of the MMF should be evaluated.", "reviewer_type": "human", "label": "error", "error_type": "Neglect", "label_origin": "expert+llm-filter"}
{"id": "prb|62|Human_3|9", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "\"there is plenty of room for improvement, not only optically wise\" (see also comment above), \"simply add some extra data processing steps...\". If the proposed improvements are as straightforward as the discussion suggests, it would be beneficial to see these implemented in the study. Alternatively, please rephrase.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_3|10", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "The discussion is very verbose on possible improvements, but not much space is used to critically discuss key limitations for the main target application.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|62|Human_3|11", "source": "prb", "split": "test", "paper_id": "prb62", "comment": "I suggest removing figure 4e unless you plan on including such recordings. Otherwise it can mislead the reader.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|63|Claude|1", "source": "prb", "split": "test", "paper_id": "prb63", "comment": "The paper compares the ONE architecture's training loss with benchmark methods in Figure 2c, whereas standard practice in the neural operator literature (including the FNO paper that the authors cite) is to report and compare test/validation errors. This methodological choice prevents a fair assessment of the model's generalization capability.\n\n\"Figure 2c shows the comparison of the training loss of our ONE architecture with other PDE solving models, including fully convolution networks (FCN) [28], principal component analysis-based neural network (PCANN) [29], reduced biased method (RBM) [30], graph neural operator (GNO) [31], low-rank kernel decomposition neural operator (LNO) [25], multipole graph neural operator (MGNO) [32], and Fourier neural operator (FNO) [24].\"\nThe paper explicitly states it is comparing \"training loss\" values. Training loss reflects how well a model fits its training data, but does not measure generalization to unseen data. A model could achieve very low training loss while overfitting and performing poorly on new data. This makes training loss an inappropriate metric for comparing machine learning methods.\n\n* Quote from the FNO paper [[1]](#citation-list): \"We use Adam optimizer to train for 500 epochs with an initial learning rate of 0.001 that is halved every 100 epochs... Table 4: Benchmarks on 2-d Darcy Flow Networks s = 85 s = 141 s = 211 s = 421... FNO 0.0108 0.0109 0.0109 0.0098\"\nThe original FNO benchmark paper (Li et al., ICLR 2021), which the authors cite as reference [24], reports test set relative L2 errors in Table 4 for the Darcy flow benchmark. The values represent the model's performance on held-out test data (200 testing instances as stated: \"we use N = 1000 training instances and 200 testing instances\"), not training loss. The paper being reviewed compares its training loss to these test error values, making the comparison fundamentally invalid.\n\n* Quote from the paper: \"We used a 10 : 1 ratio for the numbers of data in the training set and validation set, respectively.\"\nThe Methods section confirms that training and validation sets were prepared separately, yet the comparison in Figure 2c uses training loss rather than validation/test loss. Standard machine learning practice dictates that model comparisons should be based on performance metrics computed on held-out data (validation or test sets) that were not used during training to ensure a fair comparison of generalization capabilities.\n\nReferences:\n[1] Li, Z., Kovachki, N., Azizzadenesheli, K., Liu, B., Bhattacharya, K., Stuart, A., & Anandkumar, A. (2021). [Fourier Neural Operator for Parametric Partial Differential Equations](https://openreview.net/forum?id=c8P9NQVtmnO). ICLR 2021.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|63|Claude|2", "source": "prb", "split": "test", "paper_id": "prb63", "comment": "While the paper claims to demonstrate an \"optical neural engine\" that combines DONN and optical XBAR components, the experimental validation only demonstrates a single DONN kernel, with no physical implementation or end-to-end optical validation of the complete ONE architecture. The optical XBAR component is evaluated only through simulation with injected noise, not actual hardware.\n\n\"Figure 5b shows output 2D data in one DONN kernel of the Fourier space processing branch in the ONE architecture (Fig. 1a) obtained from model calculations and experimental measurements\"\nThe experimental demonstration is limited to \"one DONN kernel\" of just \"the Fourier space processing branch.\" The paper claims the architecture has four cascaded layers combining Fourier space (DONN) and real space (XBAR) processing, yet only a single DONN component is experimentally validated. This is a significant gap between the proposed architecture and what was actually demonstrated.\n\"We also evaluated the performance of the ONE architecture under different noise levels of optical XBAR structures. Specifically, we added random Gaussian noise with zero mean and varying standard deviation (Std) to the values obtained from matrix multiplications to represent hardware noise\"\nThe optical XBAR component, which is described as a core component of the ONE architecture for real space processing, is evaluated only through simulated noise injection, not actual experimental hardware. The paper acknowledges this is to \"represent hardware noise,\" meaning no actual optical XBAR system was built or tested for this work.\n\n* Quote from review of optical neural network challenges [[2]](#citation-list): \"Implementing nonlinear operations in the optical domain presents challenges, though recent research shows promise... For AI inference applications specifically this challenge is less problematic since matrix multiplication dominates the computational workload while activations represent a smaller portion, allowing specialized photonic architectures to deliver significant performance advantages even with hybrid approaches to nonlinearity.\"\nThe optical computing literature recognizes that demonstrating complete optical neural network systems is challenging. While the paper presents a compelling architectural design, the experimental validation falls significantly short of demonstrating the full system functionality. Showing a single DONN kernel rather than the complete four-layer architecture with integrated DONN and XBAR components represents a substantial gap between claims and demonstration.\n\nReferences:\n[2] Lundy-Bryan, L. (2024). [Photonic Computing: A Primer](https://stateofthefuture.substack.com/p/the-state-of-photonic-computing). State of the Future.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|63|Claude|3", "source": "prb", "split": "test", "paper_id": "prb63", "comment": "The paper claims advantages of optical computing for solving PDEs, but the nonlinear activation functions (tanh, GELU) - which are essential components of neural networks - must be performed using electronic hardware. This hybrid electro-optical requirement fundamentally limits the claimed throughput and energy efficiency advantages, yet this limitation is not adequately quantified or discussed.\n\n\"Note that the nonlinear operation is the only operation performed in electronic hardware in the ONE architecture.\"\nThe paper acknowledges that nonlinear operations require electronic hardware. However, this is significant because the architecture has four layers, each requiring a nonlinear activation after the Fourier+real space processing. This means four opto-electronic conversions per forward pass, which introduces latency, energy consumption, and synchronization complexity that undermine the claimed advantages of optical computing.\n\n* Quote from the code in `FNO_DONN_2d_v4_1_layer_32_channel_fresnel.py` (lines 158-175):\n\n```python\nx1 = self.conv0(x)\nx2 = self.w0(x)\nx = self.ratio * x1 + x2\nx = F.tanh(x)\n\nx1 = self.conv1(x)\nx2 = self.w1(x)\nx = self.ratio * x1 + x2\nx = F.tanh(x)\n\nx1 = self.conv2(x)\nx2 = self.w2(x)\nx = self.ratio * x1 + x2\nx = F.tanh(x)\n\nx1 = self.conv3(x)\nx2 = self.w3(x)\nx = self.ratio * x1 + x2\n```\nThe code shows that tanh activation is applied after each of the four Fourier-space (conv0-3) and real-space (w0-3) processing combinations. This confirms that electronic nonlinearity is invoked four times per forward pass. If this were implemented on optical hardware, it would require four optical-to-electronic conversions, potentially negating much of the speed advantage claimed.\n\n* Quote from review of optical computing challenges [[3]](#citation-list): \"Compact, robust, low-loss optical nonlinearities remain an unsolved challenge for fully all-optical networks... Bit precision is limited by device variability, insertion loss, thermal drift, crosstalk, and phase noise\"\nThe optical computing literature recognizes that achieving optical nonlinearity is a fundamental unsolved challenge. The paper's claim of \">10^5 acceleration compared to typical PDE solvers\" does not account for the overhead of repeated opto-electronic conversions required for the activation functions, which could significantly impact the actual achievable speedup.\n\nReferences:\n[3] Emergent Mind. (2024). [Photonic Neural Networks](https://www.emergentmind.com/topics/photonic-neural-networks). Topic Overview.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|63|Claude|4", "source": "prb", "split": "test", "paper_id": "prb63", "comment": "The paper claims O(1) execution cost for solving PDEs with optical hardware, but this claim is conditional on having \"large enough\" optical hardware. This qualification shifts complexity to hardware requirements rather than eliminating it, and the practical implications of this condition are not adequately addressed.\n\n\"Hence, the execution cost of solving PDEs with different scales and resolutions is invariant, meaning O(1), if the scale of the optical hardware in the ONE architecture is large enough.\"\nThe O(1) claim is explicitly qualified with the condition \"if the scale of the optical hardware is large enough.\" This is a significant caveat because it means that for any practical problem that exceeds the hardware capacity, the execution cost would no longer be O(1). The paper does not provide analysis of what hardware scale is required for different problem sizes.\n\"For example, free-space reconfigurable DONNs [20, 21, 33] and optical MVM [17] are typically implemented using spatial light modulators (SLMs) with a scale > 1000 × 1000.\"\nWhile SLMs with 1000×1000 pixels exist, this does not mean arbitrary-scale problems can be solved. The paper's benchmarks include 421×421 resolution problems, but does not address how larger scientific computing problems (which can easily exceed millions of grid points) would scale on optical hardware.\n\n* Quote from scaling analysis in optical computing [[4]](#citation-list): \"The research, published Sept. 29 in Nature Communications, addresses one of the key challenges to engineering computers that run on light instead of electricity: making those devices small enough to be practical... Optical computing can be powerful, especially in terms of energy efficiency, but if you need an optical setup that's as large as an entire room to accomplish a meaningful AI inference task, such as image classification, then your optical computer isn't very practical.\"\nRecent research on optical computing scaling laws demonstrates that there are fundamental tradeoffs between problem complexity, performance, and physical size. The paper's O(1) claim oversimplifies these tradeoffs and does not address the practical physical scaling requirements for large-scale PDE problems that scientists need to solve.\n\nReferences:\n[4] Cornell University. (2025). [Researchers reveal how small optical computers could get](https://news.cornell.edu/stories/2025/11/researchers-reveal-how-small-optical-computers-could-get). Cornell Chronicle.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|63|Claude|5", "source": "prb", "split": "test", "paper_id": "prb63", "comment": "The experimental demonstration only shows qualitative visual agreement between simulation and measured optical outputs, without quantitative error analysis comparing the actual optical hardware performance to simulation for solving PDEs. The paper does not demonstrate that the physical optical system can achieve the same numerical accuracy as the simulated model.\n\n\"Figure 5b shows output 2D data in one DONN kernel of the Fourier space processing branch in the ONE architecture (Fig. 1a) obtained from model calculations and experimental measurements, showing good agreement and experimentally validating the feasibility of the ONE architecture in solving PDEs.\"\nThe experimental validation is described as showing \"good agreement\" without quantitative metrics. For a scientific computing application where numerical accuracy is critical, qualitative visual comparison is insufficient. No numerical comparison (such as mean squared error, relative L2 error, or correlation coefficient) between the experimental measurements and simulation is provided.\n\"There are some speckles in the background of measured images, which probably originate from high-order diffraction interference, leading to numerical errors in the ONE architecture for performing regression tasks.\"\nThe paper acknowledges that the experimental system has errors (speckles) that affect numerical accuracy, but does not quantify the magnitude of these errors or their impact on PDE solution accuracy. For regression tasks like PDE solving, such errors could accumulate through the four-layer architecture and significantly degrade solution quality.\n\"This discrepancy between models and experiments can be mitigated through hardware-software co-design, such as incorporating loss functions based on experimental results for gradient calculations as demonstrated in prior works [20, 33, 35].\"\nThe paper suggests that the simulation-to-reality gap could be addressed through future co-design methods, but this work does not implement or demonstrate such mitigation. The experimental validation thus shows feasibility of optical diffraction but does not validate that the optical system can achieve the claimed accuracy for solving PDEs.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|63|GPT|1", "source": "prb", "split": "test", "paper_id": "prb63", "comment": "This paper makes performance claims (Validity, Conclusions) about the ONE architecture “outperforming traditional PDE solvers” and being “comparable with state-of-the-art ML models” based primarily on training/validation loss reporting and without clearly defined held-out test protocols or fair, like-for-like baseline comparisons in the main results (e.g., Fig. 2c).\n\n“We numerically and experimentally demonstrate the capability of the ONE architecture, which not only leverages the advantages of high-performance dual-space processing for outperforming traditional PDE solvers and being comparable with state-of-the-art ML models…”\nThis sentence asserts two strong comparative conclusions—outperforming numerical solvers and matching or beating state-of-the-art ML—yet it does not specify *what metric*, *what test set*, and *what operating point* (accuracy vs speed vs memory vs energy) is used for the comparison. In PDE surrogate modeling, it is standard to distinguish training loss, validation loss, and *test* error, and to report errors on unseen samples under a clearly defined data split. Without the test protocol and metrics, the comparative statement cannot be independently verified and risks conflating training fit with generalization. The phrase “outperforming traditional PDE solvers” is particularly problematic because numerical solvers are the ground-truth generators in most supervised PDE-learning setups, so “outperform” needs explicit framing (e.g., wall-clock at fixed error tolerance). As written, the paper’s main conclusion reads as broader than what is substantiated.\n“Figure 2c shows the comparison of the training loss of our ONE architecture with other PDE solving models… The performance of the ONE architecture is comparable with the state-of-the-art neural operators…”\nUsing *training loss* as the primary basis for claiming comparability to state-of-the-art is methodologically weak because training loss is sensitive to optimization, regularization, and potential overfitting, and it does not measure predictive accuracy on unseen inputs. Standard practice for operator-learning papers is to report test-set errors (often relative $L_2$ or similar norms) and to compare on the same train/test split. The manuscript does not, in this passage, establish that the compared models were trained/evaluated under identical splits, preprocessing, and hyperparameter budgets, so the “comparable” claim is not anchored. This is not a cosmetic reporting issue: it directly affects whether the paper’s performance conclusions are valid. If the comparisons were instead made on held-out test error, the current wording should reflect that; if not, the conclusion should be weakened.\n“We used a 10 : 1 ratio for the numbers of data in the training set and validation set, respectively.”\nThis statement describes only training and validation partitioning and does not define a separate test set (or an out-of-distribution evaluation) for the Darcy experiment, despite the earlier broad performance conclusions. In operator learning, validation is typically used for model selection and early stopping, while test is reserved for final performance reporting. Without an explicit test set and a statement that reported comparisons are test-only, it is unclear whether the reported “comparison” is actually generalization performance. This ambiguity undermines confidence in the robustness of the conclusions, especially when the paper claims comparability with multiple baselines. The absence of a clear test protocol also makes it difficult to reproduce the exact reported curves and numbers.\n```python\n# configs\nTRAIN_PATH = 'pde_dataset/piececonst_r421_N1024_smooth1.mat'\nTEST_PATH = 'pde_dataset/piececonst_r421_N1024_smooth2.mat'\n\nntrain = 1000\nntest = 20\n```\nThe released demo code evaluates Darcy with only 20 test samples, which is a very small evaluation set for supporting broad claims of “state-of-the-art” comparability across resolutions and models. Small test sizes can produce unstable estimates of relative performance and can be highly sensitive to sample selection, especially for heterogeneous PDE coefficient fields. Moreover, the paper’s narrative emphasizes multiple PDE families and scales; a small test slice in a demo script does not match that breadth. Even if the full paper used more test data, the discrepancy between the demo’s evaluation setup and the claims highlights a lack of transparency about the evaluation protocol. This directly impacts reproducibility and the reliability of the conclusions.\n“Unless otherwise specified, we use N = 1000 training instances and 200 testing instances.” [[1]](#ref1)\nThis sentence exemplifies a common practice in neural-operator literature: explicitly stating both the training and testing sample counts when reporting results. In contrast, the reviewed manuscript’s key comparison statement (Fig. 2c) is framed around training loss and does not clearly ground its claims in a test-set evaluation protocol. The gap matters because a model can have low training loss yet poor test performance, particularly when architectures differ in inductive bias. The reviewed paper should align with this standard by reporting and emphasizing held-out test errors (and their dispersion across runs or samples) when making SOTA-comparability claims. Without that, the comparison is not robust.\n“All the test errors are relative L2(D) errors on the original data.” [[4]](#ref4)\nThis sentence illustrates that closely related baselines (graph/neural-operator methods) commonly report *test* errors in a physically meaningful norm on original-scale data, which allows scientific interpretation and fair comparison. The reviewed manuscript’s emphasis on training loss (and limited description of test reporting) makes its comparisons harder to interpret and potentially misleading. Since the paper explicitly compares against neural-operator baselines, matching their evaluation conventions is important for validity. Without comparable test metrics, the statement that ONE is “comparable with the state-of-the-art neural operators” is not well supported. This is a significant methodological deficiency rather than a presentation issue.\n\nReferences:\n[1] Z. Li, N. Kovachki, K. Azizzadenesheli, B. Liu, K. Bhattacharya, A. Stuart, and A. Anandkumar, “Fourier Neural Operator for Parametric Partial Differential Equations,” arXiv:2010.08895. https://arxiv.org/abs/2010.08895\n[4] Z. Li, N. Kovachki, K. Azizzadenesheli, B. Liu, K. Bhattacharya, A. Stuart, and A. Anandkumar, “Neural Operator: Graph Kernel Network for Partial Differential Equations,” arXiv:2003.03485. https://arxiv.org/abs/2003.03485", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|63|GPT|2", "source": "prb", "split": "test", "paper_id": "prb63", "comment": "This paper makes internally inconsistent and insufficiently justified claims (Validity, Conclusions) that ONE has constant-time $\\mathcal{O}(1)$ execution “irrespective of model scales,” delivers $>10^5$ speedup over PDE solvers, and consumes $\\sim 10\\,\\mu$W static power—claims that rely on optimistic assumptions, ignore key system-level costs, and conflict with the paper’s own experimentally stated component rates.\n\n“Hence, the execution cost of solving PDEs with different scales and resolutions is invariant, meaning \\( \\mathcal{O}(1) \\), if the scale of the optical hardware in the ONE architecture is large enough.”\nThis statement asserts complexity invariance with problem scale, but the condition “if the scale of the optical hardware…is large enough” effectively shifts scaling costs into hardware footprint (SLM/detector pixel count, optics size, alignment, calibration, and bandwidth). In practice, scaling to higher spatial resolution requires proportionally larger spatial bandwidth and/or more pixels, which changes hardware cost and typically changes throughput constraints (I/O, detector readout, and modulation). Moreover, ONE includes an electronic nonlinearity step (“the nonlinear operation is the only operation performed in electronic hardware”), whose latency and bandwidth can become scale-dependent when outputs grow. Presenting the runtime as $\\mathcal{O}(1)$ risks misleading readers into thinking scale is free, rather than traded for hardware area, I/O, and calibration complexity. A more defensible claim would separate optical propagation time from system-level throughput and scaling constraints.\n“Current commercial SLMs and cameras can have rates > 1000 Hz, meaning that the inference time for one instance is < 1 ms. In contrast, it typically takes minutes to hours to numerically solve PDEs. Hence, the ONE architecture features \\( > 10^5 \\) (five orders of magnitude) acceleration compared to typical PDE solvers.”\nThis speedup claim is not supported by a controlled benchmark (same PDE, same resolution, same hardware, and clearly defined error tolerance) and therefore is not a reliable basis for conclusions. The comparison baseline “minutes to hours” is highly problem- and resolution-dependent; many 2D PDE solves at moderate grid sizes can be far faster than minutes on modern CPUs/GPUs. Additionally, the paper’s own experimental setup uses devices far below 1000 Hz (see below), which means the claimed 1 ms inference is not demonstrated and may not be achievable in the proposed configuration. Finally, the claim omits training time and dataset generation cost, which are essential when comparing ML surrogates against direct solvers for end-to-end time-to-solution. As written, the acceleration factor is closer to a speculative best-case than an experimentally or computationally validated result.\n“All transmissive SLMs are the LC 2012 model from HOLOEYE Photonics AG with a refresh rate of 60 Hz… The output data was captured on a CMOS camera with a frame rate of 34.8 frames per second…”\nThese experimentally stated component rates contradict the earlier “> 1000 Hz” premise used to justify <1 ms inference time and $>10^5$ speedup. If the system is limited by 60 Hz modulation and ~35 fps capture, the per-instance latency would be on the order of tens of milliseconds or more even before accounting for control and data transfer overhead. This inconsistency matters because the paper uses the faster rates to support headline quantitative speedup claims, while the only demonstrated hardware uses much slower devices. A rigorous treatment would either (i) report measured end-to-end throughput for the demonstrated setup, or (ii) clearly separate speculative projections from demonstrated performance with explicit assumptions and bounds. Without that, the quantitative conclusions about acceleration are not robust.\n“Hence, assuming a 10 V driving voltage, the static power consumption of SLMs is \\( \\sim 10 \\mu \\)W, which is nearly \\( 10^7 \\) (seven orders of magnitude) smaller than typical GPU inference power \\( \\sim 100 \\) W.”\nThis estimate focuses on SLM leakage current while omitting other dominant system-level power terms, including laser/source power, photodetector and readout electronics, driver electronics for modulators, control computers, and (in many photonic systems) thermal stabilization and calibration overhead. Comparing a single component’s static leakage to a whole-GPU board power is not an apples-to-apples comparison and can substantially overstate energy advantages. The manuscript also does not report uncertainty ranges (e.g., required optical power for target SNR, detector efficiency, and noise margins), which are critical for energy claims in analog optical systems. Without a full power model and clear scope boundaries, the “$10^7$ smaller” conclusion is not justified. This impacts the paper’s central motivation around energy efficiency.\n“• On a 256 ×256 grid, the Fourier neural operator has an inference time of only 0.005s compared to the 2.2s of the pseudo-spectral method used to solve Navier-Stokes.” [[1]](#ref1)\nThis sentence shows that (i) strong neural-operator baselines already benchmark speed against concrete numerical solvers and (ii) “typical PDE solver” times can be on the order of seconds for a specified grid and method rather than “minutes to hours.” The reviewed paper’s speedup claim lacks this kind of controlled comparison and therefore cannot be interpreted as a validated acceleration factor. It also highlights that fair speed claims require specifying the solver, grid, and compute hardware; otherwise, the baseline is unconstrained. If ONE’s advantage is primarily optical parallelism, the paper should still benchmark against optimized GPU/CPU solvers at matched error tolerance to quantify net speedup credibly. Without such benchmarking, the conclusions about orders-of-magnitude acceleration are not reliable.\n“This allows the linear step is performed at high speed with no energy consumption beyond transmitter and receiver energies.” [[2]](#ref2)\nThis sentence underscores that even in optimistic analyses of optical neural hardware, the relevant energy accounting includes transmitter (modulator/laser) and receiver (photodetector/readout) energies, not just passive propagation or device leakage. The reviewed manuscript’s power estimate, centered on liquid-crystal leakage current, omits these system-level costs and therefore is incomplete. In addition, transmitter/receiver energies often scale with bandwidth, SNR, and required optical power—precisely the factors that determine whether fast, accurate analog computation is feasible. Citing only SLM static leakage risks understating the energy required for real-time, high-precision regression outputs. This weakens the paper’s energy-efficiency conclusion.\n\nReferences:\n[1] Z. Li, N. Kovachki, K. Azizzadenesheli, B. Liu, K. Bhattacharya, A. Stuart, and A. Anandkumar, “Fourier Neural Operator for Parametric Partial Differential Equations,” arXiv:2010.08895. https://arxiv.org/abs/2010.08895\n[2] R. Hamerly, L. Bernstein, A. Sludds, M. Soljačić, and D. Englund, “Large-Scale Optical Neural Networks based on Photoelectric Multiplication,” arXiv:1812.07614. https://arxiv.org/abs/1812.07614", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|63|GPT|3", "source": "prb", "split": "test", "paper_id": "prb63", "comment": "This paper’s experimental section (Validity, Conclusions) does not experimentally demonstrate the full ONE architecture solving PDEs end-to-end on optical hardware; instead it validates a limited DONN subcomponent (a single Fourier-branch kernel output) and models the XBAR portion via simulated noise, making the paper’s experimental claim broader than the evidence supports.\n\n“Finally, to demonstrate the experimental feasibility of the ONE architecture, we constructed a free-space reconfigurable DONN setup and evaluated the performance of solving the Darcy flow equation under different hardware noise levels in optical XBAR structures.”\nThis sentence indicates that the physical experiment is restricted to a free-space DONN setup, while the XBAR portion is handled indirectly via “noise levels” rather than a demonstrated optical XBAR implementation. In the ONE architecture, the real-space branch and channel-mixing operations are central and are attributed to XBAR hardware; validating only the DONN branch does not establish end-to-end system behavior. The phrase “performance of solving the Darcy flow equation” suggests a full solver demonstration, but the described setup (laser + SLMs + camera) measures only an optical propagation/mapping stage. For experimental validation of an optical PDE solver, it is important to show complete input-to-solution inference with all required stages (including nonlinearities and real-space linear layers) under real hardware noise and drift. The evidence presented does not meet that bar.\n“Figure 5b shows output 2D data in one DONN kernel of the Fourier space processing branch in the ONE architecture (Fig. 1a) obtained from model calculations and experimental measurements, showing good agreement and experimentally validating the feasibility of the ONE architecture in solving PDEs.”\nThe manuscript explicitly states that the experimental validation concerns “one DONN kernel” in the Fourier branch, not the full cascaded architecture that includes repeated dual-space blocks, nonlinear operations, and XBAR-based MVM layers. Agreement on an intermediate feature map is a useful component-level check, but it does not demonstrate that the full network produces accurate PDE solutions when all stages are composed. In analog optical systems, error can accumulate across layers and across optical-electronic interfaces; validating only one kernel output does not bound end-to-end error. The conclusion that this “validat[es]…solving PDEs” is therefore overstated relative to what is experimentally shown. A stronger experimental claim would require reporting full-solution accuracy from real optical measurements, not just an internal kernel map.\n“Specifically, we added random Gaussian noise with zero mean and varying standard deviation (Std) to the values obtained from matrix multiplications to represent hardware noise, such as shot noise in photodetectors…”\nThis sentence shows that the XBAR-hardware effects are incorporated through a simplified additive-noise model applied to numerical matrix multiplications, rather than through measured noise from an actual XBAR implementation. While additive Gaussian noise can be a first-order approximation, optical XBAR noise is often signal-dependent (e.g., shot noise scaling with optical power), includes quantization and calibration errors, and can be temporally correlated due to drift. Because the paper’s conclusions about robustness to XBAR noise rely on this model, the validity of those robustness claims depends on whether the noise model matches real hardware. The manuscript does not provide evidence that the chosen model captures the dominant nonidealities of a reconfigurable XBAR at the operating regime of interest. Therefore, the “experimental demonstration” plus this simulation does not establish real-system performance.\n“The MVM results from an optical XBAR structure were uniformly randomly generated in a range of \\(-15\\) to \\(15\\)… The expected number \\( o \\) was then added with a randomly generated noise from a Gaussian distribution…”\nThis methodological detail indicates that the noise study is disconnected from a physically measured XBAR response distribution, since the “MVM results” are synthetically generated rather than derived from a modeled (or measured) optical circuit performing the relevant MVM operations. Consequently, the evaluated noise robustness may not reflect the error statistics of an actual XBAR implementation under realistic inputs, scaling, and calibration procedures. In particular, uniformly random synthetic activations may not match the heavy-tailed or structured distributions produced inside trained networks, which can change the effective sensitivity to noise. Without grounding the noise model in device physics or measurement traces, the robustness conclusion is speculative. This weakens the evidentiary basis for claims about practical feasibility.\n“Simulations of the network using models for digit- and image-classification reveal a “standard quantum limit” for optical neural networks, set by photodetector shot noise.” [[2]](#ref2)\nThis sentence highlights that, even in careful analyses of optical neural networks, photodetector shot noise can impose a fundamental performance limit that depends on optical power and detection physics. The reviewed paper’s simplified noise injection strategy and limited experimental validation do not establish that ONE operates safely above such limits for the regression accuracy demanded by scientific PDE solvers. Because PDE surrogates often require higher numerical fidelity than classification tasks, noise sensitivity can be more severe, and it is important to quantify accuracy under realistic photonic noise models. This is not to claim ONE cannot work, but rather that the current experimental evidence is insufficient to justify strong feasibility claims. A more convincing evaluation would incorporate measured noise statistics and end-to-end optical inference results.\n“In this first part, we demonstrate how these networks can be used to infer solutions to partial differential equations, and obtain physics-informed surrogate models…” [[5]](#ref5)\nThis sentence exemplifies a common framing in the PDE-learning literature: models are typically presented as *surrogates* whose validity must be demonstrated via solution-error metrics on PDE instances, not merely by showing intermediate-layer agreement. The reviewed manuscript’s experimental section largely demonstrates feasibility of a submodule (DONN) and uses simulated noise for other modules, which falls short of demonstrating a full PDE-solution surrogate running on hardware. In the context of PDE surrogates, the central experimental question is whether the model produces accurate PDE solutions under realistic constraints and noise, across a defined test set. Component-level validation is useful but not sufficient for the paper’s stated experimental claim. This supports the criticism that the experimental conclusion is broader than the evidence.\n\nReferences:\n[2] R. Hamerly, L. Bernstein, A. Sludds, M. Soljačić, and D. Englund, “Large-Scale Optical Neural Networks based on Photoelectric Multiplication,” arXiv:1812.07614. https://arxiv.org/abs/1812.07614\n[5] M. Raissi, P. Perdikaris, and G. E. Karniadakis, “Physics Informed Deep Learning (Part I): Data-driven Solutions of Nonlinear Partial Differential Equations,” arXiv:1711.10561. https://arxiv.org/abs/1711.10561", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|63|GPT|4", "source": "prb", "split": "test", "paper_id": "prb63", "comment": "The paper’s core results are not reproducible (Data and methodology; Validity) from the provided manuscript + code bundle because the paper defers data/code release (“upon publication”), the demo code requires external datasets and pretrained weights that are not included or linked, and multiple datasets are generated using proprietary tools (Ansys Lumerical, COMSOL), preventing independent reproduction.\n\n“Upon publication, all data that support the plots within this paper and other findings of this study will be available on a public GitHub repository.”\nThis statement means that, as written in the provided preprint, the data needed to reproduce the plots and quantitative results are not actually available to the reader. For a methods paper whose main claims hinge on comparative performance and hardware-feasibility estimates, access to the underlying data is essential for verification. Deferring availability to an unspecified future repository prevents third parties from checking splits, preprocessing, and exact evaluation metrics. It also blocks replication of figures that are used to support conclusions about SOTA comparability and robustness to noise. Given the strength of the claims, this is a significant reproducibility gap.\n“Upon publication, all codes that support the plots within this paper and other findings of this study will be available on a public GitHub repository.”\nSimilar to the data statement, deferring code availability makes it impossible to reproduce results at the time of reading the preprint, particularly for training pipelines, hyperparameters, and exact model architectures used for each PDE. While a code folder is included in this review package, it does not fully resolve reproducibility because key artifacts (datasets and trained weights) are still external (see below). Moreover, for optical-hardware modeling, reproducibility often requires precise device-response tables and calibration procedures, which are not clearly packaged with executable scripts. The statement therefore conflicts with the expectation that a computational methods paper should be reproducible upon release. This undermines confidence in the reported comparisons.\n“Maxwell’s equations dataset and training – We employed commercial Ansys Lumerical finite-difference-time-domain simulation software to generate an electric field dataset…”\nReliance on proprietary simulation software for dataset generation is not necessarily invalid, but it introduces a barrier to independent reproduction unless the generated datasets (or full simulation configurations) are released. Here, the manuscript does not provide the simulation project files, scripts, or complete parameterization required to regenerate the dataset without Ansys Lumerical. This matters because the generalization claims depend on the dataset distribution (e.g., rod radii sampling, boundary conditions, and time-window selection). Without accessible generation assets, an independent reader cannot verify whether the dataset matches the manuscript description. This is a major obstacle to reproducibility.\n“Multiphysics dataset and training – We employed commercial COMSOL Multiphysics finite-element simulation software to generate a temperature profile dataset…”\nThe same reproducibility concern applies here: COMSOL is proprietary, and reproducing the coupled-physics dataset requires access to the COMSOL model and detailed solver settings. The paper provides a high-level description of the circuit and pulse ranges but not the complete simulation configuration that determines the outputs used for training and evaluation. For multiphysics problems, solver tolerances, meshing, and boundary conditions can materially affect the target fields, so the inability to regenerate data prevents independent validation of model accuracy. Additionally, the dataset size is relatively small (861 samples), increasing sensitivity to exact splitting and preprocessing choices that are not fully specified. This makes the multiphysics claims difficult to reproduce or stress-test.\n“\\`pde_dataset\\` folder contains generated datasets for training and testing ONE models. Please download and unzip the \\`pde_dataset.zip\\` file from the data repository.”\nThe code README explicitly requires an external data repository for a zip file, yet it does not provide a concrete URL, DOI, or commit hash for where that repository can be accessed. Without that pointer, the provided code cannot be run to reproduce the figures or evaluate the models. This is not a minor documentation gap: it blocks execution entirely because the scripts hard-depend on those files. In reproducible ML-for-PDE work, it is standard to provide direct dataset links or to include scripts that deterministically generate the data from public sources. The absence of an actionable dataset reference undermines the reproducibility of the empirical claims.\n```python\ndata_dir = 'pde_dataset/'\nx_train = np.load(data_dir + 'train_x_last_20000_DONN.npy')\n...\nmodel_path = 'saved_model/ONE_demag.pkl'\nmodel = torch.load(model_path, map_location=device)\n```\nThis code block shows that the demos depend on local files under `pde_dataset/` and pretrained weights under `saved_model/`, neither of which are included in the reviewed package directory listing. Therefore, even “demo” reproduction requires external artifacts whose provenance and exact versioning are unspecified. In addition, this script evaluates only a small slice of the data (`x_test_norm[:128,...]`) and then saves outputs, which further emphasizes the need for precise dataset release to validate reported aggregate metrics. Without the missing files, readers cannot verify whether the models and data correspond to those used to generate the paper’s plots. This is a major reproducibility problem that affects the paper’s credibility.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|63|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb63", "comment": "The paper claims to experimentally demonstrate the capability of the ONE architecture to solve a broad range of PDEs, but the experimental validation is limited to a single component (DONN kernel) for a single time step, while the complex PDE results are purely based on software simulations.\n\n\"We numerically and experimentally demonstrate the capability of the ONE architecture in solving a broad range of PDEs in diverse disciplines, including the Darcy flow equation... the Navier-Stokes equation... Maxwell’s equations... and coupled electric current and heat transfer equations\"\nThis statement in the abstract implies that the \"experimental demonstration\" covers the \"broad range of PDEs\" listed. However, the experimental section only presents results for the Darcy flow equation (and potentially a single kernel for Navier-Stokes, as suggested by the caption but not fully detailed in the text), while the results for the complex time-dependent and multiphysics PDEs (Navier-Stokes, Maxwell, Heating) are derived from the software model (\"The ONE architecture was trained to learn... Figure 3c displays the validation loss curve...\").\n\"Figure 5b shows output 2D data in one DONN kernel of the Fourier space processing branch in the ONE architecture (Fig. 1a) obtained from model calculations and experimental measurements, showing good agreement and experimentally validating the feasibility of the ONE architecture in solving PDEs.\"\nThe experimental validation is explicitly stated to be for \"one DONN kernel\". Solving complex PDEs like Navier-Stokes requires the full architecture with multiple layers, XBARs, and nonlinearities operating in a recurrent or time-stepping manner. Validating a single linear operation (one kernel) does not validate the full system's ability to solve these PDEs, especially considering the potential for error accumulation in recurrent loops and the complexity of the full architecture which was not tested on hardware.\n\"class FNO2d(nn.Module): ... self.conv0 = SpectralConv2d(...) ... self.w0 = nn.Conv2d(...) ... x = self.ratio * x1 + x2 ... x = F.tanh(x)\"\nThe provided code confirms that the \"ONE architecture\" used for the main results is a PyTorch-based software simulation (`FNO2d`) that models the optical components. There is no evidence in the code or text that the full PDE solving process (end-to-end) was executed on the optical hardware.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|63|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb63", "comment": "The paper makes an inaccurate claim that there is \"no deployment of any optical computing systems for solving PDEs\", ignoring prior works that have proposed and demonstrated optical computing architectures for PDE solving.\n\n\"However, to date, there is no deployment of any optical computing systems for solving PDEs in any scientific domain.\"\nThis claim is factually incorrect. Prior works such as the \"Reconfigurable Optical Computer\" (ROC) [1], [5] have explicitly proposed and demonstrated optical architectures for solving partial differential equations.\n\"We introduce ROC, a reconfigurable optical computer that can solve partial differential equations (PDEs). ... We demonstrate photonic integrated circuit, which enables both analog compute-hardware...\" [1]\nThe existence of this work from 2020, which focuses on the same problem (solving PDEs) with a similar named system (\"Reconfigurable Optical Computer\"), contradicts the paper's claim of being the first. Even if the prior work was a simulation or a prototype, the ONE paper is also largely a simulation with a prototype component, so the distinction does not justify the \"no deployment\" claim.\n\nReferences:\n[1] [A Reconfigurable Optical Computer for Simulating Physical Processes](https://dl.acm.org/doi/abs/10.1145/3380944)\n[5] [Reconfigurable Optical Computer for Solving Partial Differential Equation](https://scholarspace.library.gwu.edu/concern/gw_etds/gm80hw10r)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|63|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb63", "comment": "The paper claims that the ONE architecture shows \"comparable and better performance\" than other ML models, but this claim is unsubstantiated as ONE is essentially an optical implementation of the Fourier Neural Operator (FNO) and no evidence is provided to show it outperforms the standard FNO in terms of accuracy.\n\n\"The ONE architecture not only outperforms traditional PDE solvers because of its data-driven nature, but also shows comparable and better performance with other ML models while with substantial hardware advantages because of its implementation in the optical domain.\"\nThe paper uses an architecture based on the Fourier Neural Operator (FNO) [2], as evidenced by the code class `FNO2d` and the dual-space processing description. Since ONE is an optical implementation of FNO, its algorithmic performance (accuracy) should be at best similar to FNO (and likely worse due to analog noise and limited precision). The paper does not provide a direct comparison (e.g., a table) showing that ONE achieves lower error than a standard software-based FNO or other ML models like DeepONet [3]. Therefore, the claim of \"better performance\" (if referring to accuracy) is unsupported. If referring to speed, it overlaps with the hardware advantage claim, but the \"better performance with other ML models\" phrasing usually implies accuracy in this context.\n\nReferences:\n[2] [Fourier Neural Operator for Parametric Partial Differential Equations](https://arxiv.org/abs/2010.08895)\n[3] [Deeponet: Learning nonlinear operators for identifying differential equations based on the universal approximation theorem of operators](https://arxiv.org/abs/1910.03193)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|63|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb63", "comment": "The paper's estimation of power consumption and throughput is misleading because it considers only the optical component (SLM) leakage and refresh rate, ignoring the significant power and latency overhead of the necessary peripheral electronics (lasers, cameras, control systems).\n\n\"The power consumption is mainly determined by the leakage current of liquid crystal cells in SLMs. ... the static power consumption of SLMs is ~ 10 \\mu W, which is nearly 10^7 (seven orders of magnitude) smaller than typical GPU inference power ~ 100 W.\"\nThis comparison is highly misleading. A functional optical computing system requires a light source (laser) which consumes milliwatts to watts, a camera/detector which consumes watts, and a control computer/FPGA to drive the SLMs and process the camera output, which also consumes watts. Comparing the leakage current of the SLM alone (10 µW) to the total power of a GPU (100 W) ignores the majority of the power consumption in the optical system, resulting in an exaggerated efficiency claim.\n\"Current commercial SLMs and cameras can have rates > 1000 Hz, meaning that the inference time for one instance is < 1 ms.\"\nThis estimate ignores the system latency including data transfer (PC to SLM), liquid crystal response time, camera exposure and readout time, and the electronic processing steps (nonlinear activation, addition) required between layers. For a multi-layer architecture like ONE, these latencies accumulate. A 1 ms inference time implies a 1 kHz end-to-end system speed, which is optimistic given the synchronization and I/O overheads in hybrid optical-electronic systems.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|63|Gemini|5", "source": "prb", "split": "test", "paper_id": "prb63", "comment": "The noise analysis uses an undefined \"0.5 Std\" metric to claim robustness, which is scientifically ambiguous and potentially misleading given the likely signal scale of the neural network.\n\n\"The current hardware implementation... can achieve quite a small noise level similar or below the noise level corresponding to 0.5 Std. Hence, the noise influence in optical XBAR structures on the performance of the ONE architecture is not substantial.\"\nThe metric \"0.5 Std\" is not clearly defined (e.g., is it 0.5 times the standard deviation of the signal, or an absolute standard deviation of 0.5?). Given that the network uses `tanh` activations (range [-1, 1]), the signal values are likely in the order of unity. If \"0.5 Std\" refers to an absolute noise standard deviation of 0.5, this represents a very low Signal-to-Noise Ratio (SNR), which would typically degrade performance significantly. The claim that such a high noise level is \"not substantial\" contradicts standard understanding of analog computing precision and requires a more rigorous definition of the noise model and signal scaling.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|63|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb63", "comment": "What nonlinear functions are used in the demonstrated architecture (Fig. 1a)? Please discuss about it.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|63|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb63", "comment": "In Fig. 3e, it looks like the relative error figure shows a few sharp lines while there are no such lines in the absolute error. Can authors comment on the reason?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|63|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb63", "comment": "In the first paragraph of page 6, the used symbol of big O notation has different format from those in the experimental demonstration section. Please revise it.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|63|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb63", "comment": "What's the output power of laser diode in the experiment?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|63|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb63", "comment": "The claim in the abstract “Although optical systems offer high-throughput and energy efficient ML hardware, there is no demonstration of utilizing them for solving PDEs” and related claims in the text are wrong. Please see the following works. I would recommend the authors amend their claims.\n\nY. Zhao et al. “Real-Time FJ/MAC PDE Solvers via Tensorized, Back-Propagation-Free Optical PINN Training” arXiv:2401.00413 [cs.LG], 2023. https://arxiv.org/abs/2401.00413.\n\nY. Zhao et al. “Experimental Demonstration of an Optical Neural PDE Solver via On-Chip PINN Training” arXiv:2501.00742 [cs.LG], 2025. https://arxiv.org/abs/2501.00742.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|63|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb63", "comment": "“Specifically, we performed quantitative scaling analyses of energy consumption and throughput of the optically implemented ONE architecture and electronically implemented FNO, with the latter having shown the best prediction and speed performance over other models” -> Is \"latter\" a typo?", "reviewer_type": "human", "label": "error", "error_type": "Unstated statement", "label_origin": "expert+llm-filter"}
{"id": "prb|63|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb63", "comment": "The energy scaling analysis on page 14 does not account for meeting the photodetector/camera minimum signal-to-noise ratio which may be at risk for very large diffractive optical neural network systems without also scaling laser power. This should account for optical fan-out, any worst-case insertion (transmissive) losses, and any amplification that may need to be done with increased depth to remain within dynamic range of the SLM. Can the authors comment on their expectations for these practical scaling considerations?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|63|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb63", "comment": "I would recommend the authors perform an additional baseline comparing the performance of training only the CNN from Fig. 5 on the Darcy Flow and Navier Stokes datasets, in comparison to the current case that uses the experimental hardware in tandem with the postprocessing CNN. If the CNN has similar performance on its own, it will seem pointless to adopt the tandem experimental system. Furthermore, I would recommend the authors amend their energy/speed analysis to account for any digital post-processing that needs to be done. If the authors disagree, alternatively, please explain how experimental systems much larger than theirs will not also require digital error corrections.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|63|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb63", "comment": "Can the authors clarify whether the full ONE architecture (DONN + XBAR) was implemented in their experiments of Fig. 5, or only the DONN piece of the architecture? It appears that this is the case as mentioned in Methods, but it was not completely clear in the main text. Furthermore, can the authors clearly label simulated results and experimental results in all figures, particularly Fig. 5? The authors place most emphasis in this paper on simulations of ONE performance (which, mathematically speaking, is essentially just a 2D FNO architecture) rather than experiments; this fact should be made clear to the reader.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|64|Claude|1", "source": "prb", "split": "test", "paper_id": "prb64", "comment": "The paper describes a confidence-based ensemble weighting formula (Equation 3) that is mathematically inconsistent with the actual implementation in the provided code, making the methodology non-reproducible from the paper description alone.\n\n\"Each subnetwork of the ensemble network calculates the average confidence level of one predicted instance as: c = (1/N) * sum(|P_i - 0.5| + 0.5), where P_i represents the predicted value of pixel i from the subnetwork, which is binarized to be either 0 or 1\"\nAccording to this description, if P_i is truly binarized to values of 0 or 1 as stated, then |P_i - 0.5| would always equal 0.5 for every pixel. This means the confidence c would always equal (1/N) * sum(0.5 + 0.5) = 1.0 for all predictions, regardless of the actual prediction values. This would make the confidence measure completely uninformative and unable to distinguish between high-confidence and low-confidence predictions, which contradicts the stated purpose of confidence-based ensemble weighting.\nThe code implementation in model_cotrain.py (lines 17-25):\n```python\ndef confidenceFactor(arr):\n    median = 0.5\n    confList = []\n    for i in range(0, arr.shape[0]):\n        conf = np.sum(np.abs(arr[i] - median)*1.8 + 0.1) / arr.shape[-1]\n        confList.append(conf)\n    meanConf = np.mean(confList)\n    return confList, meanConf\n```\nThe actual implementation uses different coefficients (multiplying by 1.8 and adding 0.1) compared to the paper's formula (multiplying by 1 and adding 0.5). Furthermore, the code operates on raw continuous predictions (arr[i]) before binarization, not on binarized values as the paper explicitly states. This represents a fundamental discrepancy between the published methodology and the actual implementation, which affects the reproducibility of the work. A verification script confirms that with truly binarized inputs, the paper's formula produces a constant value of 1.0 regardless of prediction quality.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|64|Claude|2", "source": "prb", "split": "test", "paper_id": "prb64", "comment": "The paper characterizes the approach as \"self-supervised dynamic learning\" in the title and abstract, but the method requires a substantial amount of initially labeled data (20,000 samples) for pre-training, which is inconsistent with the standard definition of self-supervised learning.\n\n\"In this paper, we present a self-supervised dynamic learning approach that achieves long-term, high-fidelity transmission of arbitrary optical fields through unstabilized MMFs.\"\nThe paper's title and abstract explicitly claim a \"self-supervised\" approach. However, self-supervised learning in the machine learning community typically refers to methods that learn representations from unlabeled data using pretext tasks (e.g., predicting missing parts, contrastive learning) without requiring any labeled data for the primary task. As defined in the literature, \"Self-supervised learning (SSL) is a type of unsupervised learning that helps in the performance of downstream computer vision tasks... the motivation behind SSL is to learn useful depictions of the data from unlabeled data by making use of the self-supervision concept\" [[4]](#citation-list). The method described in this paper is more accurately characterized as semi-supervised learning with pseudo-labeling, which is a fundamentally different paradigm.\n\"At the preparation stage of data transmission, a sequence of known patterns is transmitted, and the MMDN is statically trained on the initial instances.\"\nThe paper acknowledges that an initial training phase with known (labeled) patterns is required. This contradicts the self-supervised characterization, as true self-supervised methods do not require such labeled initialization.\nFrom the code MMDN.py (line 20): `parser.add_argument(\"--sizeOfPretrain\", type=int, default=20000, help=\"number of pre-training dataset\")`\nThe default configuration requires 20,000 labeled samples for pre-training. This is a substantial amount of labeled data that is far from self-supervised. The paper's claim in the abstract that \"network parameters are dynamically updated over time in a self-supervised manner, by learning from currently predicted pseudo-labels\" conflates pseudo-label self-training (a semi-supervised technique) with true self-supervised learning. According to standard terminology, as explained in [\"Semi-supervised learning, i.e. jointly learning from labeled and unlabeled samples\"](https://arxiv.org/pdf/1908.02983) [[1]](#citation-list), pseudo-labeling is a form of semi-supervised learning, not self-supervised learning.\n\nReferences:\n[1] Arazo, E., Ortego, D., Albert, P., O'Connor, N. E., & McGuinness, K. (2020). [\"Pseudo-Labeling and Confirmation Bias in Deep Semi-Supervised Learning.\"](https://arxiv.org/abs/1908.02983) IEEE International Joint Conference on Neural Networks (IJCNN), 2020.\n[4] Jaiswal, A., Babu, A. R., Zadeh, M. Z., Banerjee, D., & Makedon, F. (2021). [\"A Survey on Contrastive Self-Supervised Learning.\"](https://arxiv.org/abs/2011.00362) Technologies, 9(1), 2.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|64|Claude|3", "source": "prb", "split": "test", "paper_id": "prb64", "comment": "The paper's experimental comparisons are limited to a \"StaticNN\" baseline (which is the same architecture without dynamic updates) and lack direct comparison with other state-of-the-art methods for handling perturbations in multimode fiber imaging, weakening the paper's claims of comprehensive improvement.\n\n\"The static neural network (StaticNN) trained on the first 500-second data and tested on the following 500-second is taken as the baseline method.\"\nThe primary comparison throughout the paper is against StaticNN, which is essentially the same architecture without the dynamic update mechanism. While this demonstrates the benefit of dynamic updates, it does not establish how the proposed method compares to other existing approaches that address similar challenges.\n\"We compared MMDN with previous approaches in terms of time duration, reconstruction quality, and transmission distance, etc., and demonstrated a comprehensive improvement of our approach (see Supplementary Fig. 7).\"\nThe paper claims comprehensive improvement but references a supplementary figure for these comparisons. There is no direct experimental comparison in the main text with methods like the \"configuration training\" approach by Resisi et al. (2021) [[2]](#citation-list), who demonstrated that deep learning can generalize over strongly perturbed fibers by training on multiple fiber conformations. Their work achieved a factor of ~3.5 improvement in reconstruction fidelity using a U-Net architecture with configuration training, which represents a relevant baseline for handling fiber perturbations.\n\"Another inspiring approach is to use the mixture-of-expert framework... This architecture has been successfully applied for image denoising and phase retrieval to improve reconstruction accuracy and robustness to noise.\"\nThe paper cites the Dynamic Synthesis Network (DSN) approach by Tahir et al. (2022) [[3]](#citation-list) as reference [18] and [25], which uses a similar multi-network ensemble for adaptive descattering. However, no direct experimental comparison with DSN is provided. Given that DSN also addresses dynamic adaptation to scattering media variations through an ensemble of networks, a direct comparison would significantly strengthen the validation of the claimed improvements.\n\nReferences:\n[2] Resisi, S., Popoff, S. M., & Bromberg, Y. (2021). [\"Image Transmission Through a Dynamically Perturbed Multimode Fiber by Deep Learning.\"](https://onlinelibrary.wiley.com/doi/full/10.1002/lpor.202000553) Laser & Photonics Reviews, 15(10), 2000553.\n[3] Tahir, W., Wang, H., & Tian, L. (2022). [\"Adaptive 3D descattering with a dynamic synthesis network.\"](https://www.nature.com/articles/s41377-022-00730-x) Light: Science & Applications, 11, 42.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|64|Claude|4", "source": "prb", "split": "test", "paper_id": "prb64", "comment": "The paper acknowledges the challenge of error accumulation in pseudo-label-based learning but does not describe or implement explicit mechanisms to mitigate confirmation bias, which is a well-documented problem in pseudo-labeling approaches.\n\n\"The dynamic learning strategy for MMF dynamics modeling intuitively raises a critical demand for accurate inference on current batch, so as to provide reliable training sets for the subsequent update. However, two main factors exist that could hinder its naïve implementation from practical usage. First of all, the inevitable inference error for previous batch induces a bias to the model update, which will accumulate and largely deteriorate the network effectiveness after a long period.\"\nThe paper explicitly acknowledges the problem of error accumulation and bias in the pseudo-label learning approach. However, the proposed solution (multi-scale memory ensemble) addresses this primarily through model ensembling rather than through established techniques specifically designed to prevent confirmation bias in pseudo-labeling.\n\"Models trained using self-generated pseudo-labels generally suffer from confirmation bias, where the model keeps amplifying its own errors.\" — from Arazo et al. (2020) [[1]](#citation-list)\nThe semi-supervised learning literature has extensively documented confirmation bias in pseudo-labeling approaches. Arazo et al. demonstrated that without proper regularization techniques such as mixup augmentation, minimum labeled samples per mini-batch, and dropout, pseudo-labeling approaches suffer from severe confirmation bias. The MMDN method relies solely on confidence-based weighting and forgetting mechanisms for short-term networks, without incorporating these established techniques for bias mitigation.\nFrom model.py (lines 5-21), the network architecture:\n```python\ndef createCNN(outsize, input_shape):\n    model_input = Input(shape=input_shape)\n    x = Conv2D(8, kernel_size=(3, 3), activation='relu')(model_input)\n    x = BatchNormalization(axis=-1)(x)\n    x = Dropout(0.4)(x)\n    x = Conv2D(8, kernel_size=(3, 3), strides=2, activation='relu')(x)\n    x = BatchNormalization(axis=-1)(x)\n    x = Dropout(0.4)(x)\n    x = Flatten()(x)\n    x = Dense(outsize, activation='sigmoid')(x)\n    cnn = Model(inputs=model_input, outputs=x)\n    return cnn\n```\nWhile the code includes dropout (0.4), the paper does not discuss whether dropout is disabled during pseudo-label generation, which is critical for preventing noisy pseudo-labels. Furthermore, the paper does not employ data augmentation or mixup during training, which have been shown to be effective regularizers against confirmation bias. The absence of these techniques raises concerns about the long-term stability of the self-training loop, particularly for the claimed >1000 second operation.\n\nReferences:\n[1] Arazo, E., Ortego, D., Albert, P., O'Connor, N. E., & McGuinness, K. (2020). [\"Pseudo-Labeling and Confirmation Bias in Deep Semi-Supervised Learning.\"](https://arxiv.org/abs/1908.02983) IEEE International Joint Conference on Neural Networks (IJCNN), 2020.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|64|GPT|1", "source": "prb", "split": "test", "paper_id": "prb64", "comment": "This paper’s confidence-based ensemble algorithm (the “Confidence-based ensemble algorithm” equations for computing confidence and weights) is specified in a way that becomes degenerate/undefined for the stated binarized predictions, calling into question the validity of the core MMDN ensembling mechanism that underpins the reported long-term accuracy.\n\n“Each subnetwork of the ensemble network calculates the average confidence level of one predicted instance as:”\n\n  $$\\begin{array}{c}c=\\frac{1}{N}\\sum _{i=1}^{N}\\left(\\left|{P}_{i} -0.5\\right|+0.5\\right) ,\\#(3.)\\end{array}$$\n\n  “where ${P}_{i}$ represents the predicted value of pixel $i$ from the subnetwork, which is binarized to be either 0 or 1, and $N$ is the spatial resolution of the input patterns.”\nIf $P_i$ is binarized to 0 or 1, then the term $|P_i-0.5|+0.5$ equals 1 for every pixel, making $c=1$ for every instance regardless of model quality. A confidence metric that is constant cannot discriminate between experts, so it cannot serve as a gating signal for adaptive ensembling. This is not a cosmetic issue: the ensemble gate is the paper’s main mechanism for robustness to drift and jitter, so a degenerate confidence definition undermines the method’s stated rationale. Moreover, the text explicitly ties the method’s adaptability to this grading module, so the correctness of this definition is central to the paper’s validity. Without a non-degenerate confidence, the method reduces to either a fixed average or an undefined weighting. The paper does not provide an alternative, non-binarized formulation in the main manuscript.\n“The confidence-based weight of each subnetwork is defined as:”\n\n  $$\\begin{array}{c}{w}_{k}=\\text{exp}\\left(\\frac{1-{c}_{k}}{\\left(1-{c}_{1}\\right)+\\left(1-{c}_{2}\\right)+\\left(1-{c}_{3}\\right)}\\right). \\#(4.)\\end{array}$$\nWith $c_k$ forced to 1 by the paper’s own binarization statement, the denominator $(1-c_1)+(1-c_2)+(1-c_3)$ becomes 0, so the exponent is undefined (division by zero). That implies the weighting rule, as written, cannot be executed in the regime the paper claims to use (binary spatial patterns with binarized outputs). Even if one assumes non-binarized $P_i$, the paper does not clarify how $c_k$ is kept away from 1 to avoid numerical instability, which is essential for a stable online system. Because these weights directly determine the final prediction $P$, any undefined or unstable gating would directly impact the reported “~100% accuracy throughout the 1000s period.” The manuscript does not acknowledge this degeneracy or provide implementation details that resolve it. This creates a gap between the mathematical description and an operational algorithm, which is a major methodological flaw.\n```python\n# return confidence level, 0.1~1.0\ndef confidenceFactor(arr):\n    median = 0.5\n    confList = []\n    for i in range(0, arr.shape[0]):\n        conf = np.sum(np.abs(arr[i] - median)*1.8 + 0.1) / arr.shape[-1]\n        confList.append(conf)\n    meanConf = np.mean(confList)\n    return confList, meanConf\n\n# confidence based weight\ndef weightFactor(conf1, conf2, conf3):\n    w1 = np.exp(10 * (2 - conf2 - conf3) / (3 - conf1 - conf2 - conf3))\n    w2 = np.exp(10 * (2 - conf1 - conf3) / (3 - conf1 - conf2 - conf3))\n    w3 = np.exp(10 * (2 - conf1 - conf2) / (3 - conf1 - conf2 - conf3))\n    return w1, w2, w3\n```\nThe released code implements a different confidence computation (continuous-valued predictions relative to 0.5, scaled into roughly [0.1, 1.0]) and a different weight function (with a factor of 10 and a distinct functional form) than the paper’s equations. This discrepancy matters because the gate’s behavior (how sharply it selects experts, and how it behaves near “high confidence”) is highly sensitive to the chosen mapping and scaling. The code also avoids the “binarized $P_i$” degeneracy by operating on raw predicted probabilities rather than binarized values, contradicting the manuscript’s textual definition. Since the paper’s central claim is that adaptive ensembling stabilizes self-supervised updates over long times, the lack of agreement between the written method and the executable method undermines interpretability and reproducibility of the main result. At minimum, readers cannot determine which algorithm produced the reported figures without additional clarification. This is a validity issue because it is unclear which procedure is being evaluated.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|64|GPT|2", "source": "prb", "split": "test", "paper_id": "prb64", "comment": "This paper claims online self-supervised learning from unlabeled streaming data, but the provided implementation performs per-update training with labeled validation data and early stopping on validation loss, which is incompatible with the stated unlabeled setting and can inflate reported performance.\n\n“The MMDN model will be dynamically updated by online training on the unlabeled streaming data using predicted input images as labels, hence working in a self-supervised architecture.”\nThis sentence asserts that streaming data are unlabeled and that the model updates rely on pseudo-labels, which implies that ground-truth labels are not available during online operation. In such a regime, the update procedure must be specified so it can run without any access to the true $y$ for the incoming batches. The manuscript does not describe using labeled validation data or any proxy criterion for early stopping or update scheduling. Because the entire contribution is framed around long-term deployment in an “unstabilized” channel, whether updates require labels is central to validity, not an implementation detail. If labels are required to tune or stop updates, the method is no longer self-supervised in the stated sense. This mismatch affects how credible and transferable the reported long-term performance is to real-world settings.\n```python\ndef get_callbacks():\n    early_stopping = EarlyStopping(monitor='val_loss', min_delta=5e-6, patience=10, verbose=2, mode='min') # min_delta=5e-6\n    csv_logger = CSVLogger('./log.csv', append=True)\n    tensorboard = TensorBoard(log_dir='./logs', histogram_freq=0, write_graph=False)\n    return [tensorboard, csv_logger, early_stopping]\n```\nMonitoring `val_loss` for early stopping requires access to ground-truth labels for the validation set, which contradicts the claimed “unlabeled streaming data” online update scenario. In an online self-supervised setting, validation labels for each incoming time window typically do not exist, so an algorithm must rely on unsupervised consistency criteria or other proxies rather than supervised validation loss. Using labeled validation for early stopping is not just a convenience: it changes the training dynamics by adaptively selecting the amount of optimization based on ground truth. That can substantially improve apparent performance and stability compared to a truly unlabeled update loop. Since the paper’s key claim is “self-supervised dynamic updating,” this code-level dependence on supervised validation indicates the reported procedure is not the one described. The manuscript does not explain how early stopping would be done without labels.\n```python\n    elif flag_dynamic_learning:\n        print(\"=\"*10 + \" Network update \" + \"=\"*10)\n        print(\"-\"*4 + \"> model 3\")\n        clf3.fit(x_labeled[-sizeOfBatch:], y_labeled[-sizeOfBatch:], batch_size=batch_size, epochs=int(epochs), callbacks=get_callbacks(),validation_data=(x_fortest, y_fortest))\n        if flag_multi_model:\n            print(\"-\"*4 + \"> model 2\")\n            clf2.fit(x_labeled[-sizeOfBatch:], y_labeled[-sizeOfBatch:], batch_size=batch_size, epochs=int(epochs), callbacks=get_callbacks(), validation_data=(x_fortest, y_fortest))\n        else: \n            clf2 = clf3\n        if flag_multi_model:\n            print(\"-\"*4 + \"> model 1\")\n            clf1.fit(x_labeled[-sizeOfBatch:], y_labeled[-sizeOfBatch:], batch_size=batch_size, epochs=int(epochs), callbacks=get_callbacks(), validation_data=(x_fortest, y_fortest))\n        else:\n            clf1 = clf3\n```\nThe implementation repeatedly supplies `(x_fortest, y_fortest)` as validation data at every online update step, implying that the true labels for each time batch are known at update time. This contradicts the manuscript’s description of unlabeled streaming adaptation and changes the problem from self-supervised adaptation to a supervised (or semi-supervised) online learning setting. Because the callback includes early stopping on `val_loss`, these ground-truth labels can influence when training stops, which is a form of label leakage into the update schedule. Additionally, the same `y_fortest` is later used for reporting accuracy on that batch, so the evaluation is not cleanly separated from update-time model selection decisions. In optics/communication experiments, such leakage can materially overestimate real deployment performance, especially in long horizons where stopping criteria strongly affect drift. The paper does not report results for an update loop that removes this dependency.\n“On ImageNet, we first train an EfficientNet model on labeled images and use it as a teacher to generate pseudo labels for 300M unlabeled images. We then train a larger EfficientNet as a student model on the combination of labeled and pseudo labeled images.” [4](#ref4)\nThis description exemplifies a standard self-training setup where unlabeled inputs receive pseudo labels generated by a teacher model and are then used for training, keeping the unlabeled portion label-free by definition. The key point for this paper is that self-training does not assume ground-truth labels are available for the unlabeled stream; evaluation and selection are typically handled separately. In contrast, the reviewed implementation injects per-batch ground-truth labels via `validation_data` and then uses those labels for early stopping, meaning the online procedure is not operating in the same information setting described in the manuscript. While using labeled validation is legitimate in a supervised online benchmark, it should be stated explicitly because it changes the claim from self-supervised to supervised adaptation. Without such clarity, the reader cannot assess whether the reported long-term performance would hold when labels are truly absent. This weakens the validity of the paper’s central claim about self-supervised deployment.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|64|GPT|3", "source": "prb", "split": "test", "paper_id": "prb64", "comment": "The provided code and documentation do not enable reproduction of the experimental results because critical datasets are not specified/provided in a reproducible way and the code contains an import that is incompatible with standard scikit-learn, preventing execution.\n\n~~~~markdown\n## Usage\n```\n$ python MMDN.py\n```\n~~~~\nThe code documentation provides only a one-line invocation and does not specify the required Python/TensorFlow/scikit-learn versions, the expected dataset format, or how to obtain the experimental data. For computational imaging papers, reproducibility typically requires (at minimum) a concrete data download/preprocessing recipe and an environment specification so that a third party can run the pipeline. Here, there is no description of where the required `.npy` files come from, how they relate to the experiments in Fig. 2–5, or what license/availability constraints apply. This omission is material because the reported results are quantitative and depend on long temporal sequences of speckle/pattern pairs. Without clear data provenance and setup instructions, reviewers cannot verify the claimed “>99.9% accuracy… over 1000 seconds.” The minimal README therefore falls short of common reproducibility practice.\n```python\nparser = argparse.ArgumentParser()\nparser.add_argument(\"--datafolder\", type=str, default=\"../Data/Testdata_bin32\")\nparser.add_argument(\"--saverootfolder\", type=str, default=\"../Data/Testdata_bin32/result\")\nparser.add_argument(\"--use_model\", type=str, default=\"pretrain\", help=\"pretrain model prefix\")\nparser.add_argument(\"--modelfolder\", type=str, default=\"../Data/Testdata_bin32/model\")\nparser.add_argument(\"--configFile\", type=str, default=\"./config.yaml\")\n```\n\n```python\n# load target pattern\ndataLabels = np.load(os.path.join(datafolder, 'pattern.npy')).astype(np.uint8)\noutsize = dataLabels.shape[1]\n\n# load input speckle\ndataValues0 = np.load(os.path.join(datafolder, 'speckles.npy')).astype(np.uint8)\n```\nThe main script hard-codes a default data path (`../Data/Testdata_bin32`) and requires `pattern.npy` and `speckles.npy` to exist in that folder. These files are not part of the provided `preprint/code/` directory structure, and the paper does not provide a reproducible procedure to generate them from publicly available sources. Because the results depend on temporal drift and jitter behavior, substituting arbitrary data is not sufficient to verify the claims; the dataset must correspond to the described unstabilized 100 m and 1 km MMF measurements. In addition, there is no schema description (shape, dtype, normalization) beyond the `astype(np.uint8)` casting, which is insufficient for replicating preprocessing choices. This creates a direct barrier to reproducing any figure or table quantitatively. Consequently, the methodological reporting is not transparent enough to enable independent verification.\n```python\nfrom sklearn.metrics import accuracy_score, compare_mse\n```\nThis import makes the code non-executable in standard environments where `sklearn.metrics` does not expose a `compare_mse` symbol. Because this import occurs at module import time, it prevents running any part of the pipeline even if the MSE path is never used (e.g., `graylevel=2`). This is not a minor dependency mismatch: it blocks the primary entry point (`python MMDN.py`) from running at all without manual code edits. A reproducible release should include a pinned environment and tested imports, especially given the paper’s emphasis on a deployable dynamic learning pipeline. The presence of such a blocking import indicates the released code was not packaged in a way that supports third-party reproduction. This directly affects confidence in the reported experimental outcomes.\n[5](#ref5)\n\n```python\nfrom sklearn.metrics._regression import (\n    d2_absolute_error_score,\n    d2_pinball_score,\n    d2_tweedie_score,\n    explained_variance_score,\n    max_error,\n    mean_absolute_error,\n    mean_absolute_percentage_error,\n    mean_gamma_deviance,\n    mean_pinball_loss,\n    mean_poisson_deviance,\n    mean_squared_error,\n    mean_squared_log_error,\n    mean_tweedie_deviance,\n    median_absolute_error,\n    r2_score,\n    root_mean_squared_error,\n    root_mean_squared_log_error,\n)\n```\nThe scikit-learn project’s public `sklearn.metrics` initializer lists many exported regression metrics (including `mean_squared_error`) but does not export `compare_mse` in the same manner. This supports the claim that `compare_mse` is not part of the standard `sklearn.metrics` public API, so the paper’s code will fail for typical scikit-learn installations. In a reproducibility context, relying on non-existent public symbols without documenting a custom fork or a specific historical version is a major issue. It forces reviewers to guess how to patch the code (e.g., replacing with `mean_squared_error` or a different library), which can change evaluation behavior. Because the paper reports extremely low error rates (down to 2e-6), even small metric/threshold differences can matter. The paper does not document any such required patching, reinforcing that the released materials are insufficient for faithful reproduction.\n\nReferences:\n[1] [Shachar Resisi, Sebastien M. Popoff, and Yaron Bromberg. “Image Transmission Through a Dynamically Perturbed Multimode Fiber by Deep Learning.” *Laser & Photonics Reviews* 15, 2000553 (2021).](https://ui.adsabs.harvard.edu/abs/2021LPRv...1500553R/abstract)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|64|GPT|4", "source": "prb", "split": "test", "paper_id": "prb64", "comment": "The paper’s main claims (abstract and discussion) overstate the scope of what is demonstrated, because the described experimental setup and learning objective target binary amplitude pattern recovery rather than arbitrary optical fields (e.g., complex field transmission) or direct high-resolution video transmission, weakening the robustness of the paper’s conclusions.\n\n“In this paper, we present a self-supervised dynamic learning approach that achieves long-term, high-fidelity transmission of arbitrary optical fields through unstabilized MMFs.”\n“Arbitrary optical fields” is a strong claim in fiber transmission, because an optical field generally refers to a complex-valued amplitude (magnitude and phase) rather than a binary amplitude pattern. The rest of the manuscript, however, describes an amplitude-only modulation and an intensity-speckle measurement pipeline paired with binary classification-style losses, which is a narrower problem. Without measuring phase or explicitly representing complex fields, the method cannot be assumed to transmit “arbitrary optical fields” in the broader sense used in wave optics. This matters for validity because the claimed application space (general remote imaging/communication of optical fields) is broader than what is experimentally validated. Readers may interpret the claim as complex field recovery, which is not supported by the provided methodological description. The paper does not delimit the claim to binary amplitude patterns in the abstract.\n“We used a binary SLM as the amplitude modulator to encode the spatial information, and the output speckles are captured by the monochromatic CMOS.”\n\n  “Our research employed arbitrary random binary images, as well as natural scene images including the Fashion-MNIST dataset, Latin letters from the E-MNIST dataset, and handwritten digitals from the MNIST dataset. The input images tested in the experiments are of 16×16-pixel and 32×32-pixel resolution.”\nThese statements indicate the demonstrated system encodes binary amplitude patterns and evaluates recovery on low-resolution binary images (and binarized versions of standard datasets). This is materially different from demonstrating recovery of arbitrary grayscale amplitudes or complex optical fields, both of which are common interpretations of “arbitrary optical fields.” The limitation is not just resolution; it is also the signal alphabet and modulation model, which constrains what kinds of “fields” are being transmitted and recovered. While binary pattern transmission is still valuable for communications, the manuscript’s broad framing suggests a more general optical-field capability than is actually tested. This gap affects how the results should be interpreted and compared to other optical-field transmission approaches. The paper does not provide experiments that vary gray level or recover complex-valued fields.\n```python\nclf1 = createCNN(outsize=outsize, input_shape=input_shape)\nclf1.compile(loss=keras.losses.binary_crossentropy, optimizer=ada)\n```\n\n```python\n    x = Flatten()(x)\n    x = Dense(outsize, activation='sigmoid')(x)\n```\nThe use of `binary_crossentropy` and a `sigmoid` output layer is consistent with per-pixel Bernoulli (binary) prediction rather than regression of continuous-valued amplitudes or complex fields. This reinforces that the implemented learning objective is tailored to binary pattern recovery, aligning with the manuscript’s “random binary patterns” experiments. A binary objective can yield high “accuracy” even when subtle analog distortions exist, which is relevant when the paper extrapolates to high-fidelity transmission more broadly. If the goal is truly “arbitrary optical fields,” the method would need to specify a representation and loss appropriate for complex amplitudes (or at least continuous intensities) and demonstrate performance accordingly. Without that, the conclusion should be scoped to binary amplitude pattern transmission. The mismatch between broad abstract claims and the binary-coded implementation weakens the conclusions.\n“We experimentally measure the monochromatic transmission matrix (TM) of an optical multiple scattering medium using a spatial light modulator together with a phase-shifting interferometry measurement method.” [3](#ref3)\nThis statement illustrates that approaches aimed at controlling or characterizing an optical medium at the “field” level often require phase-sensitive measurement (e.g., interferometry) to recover complex transmission properties. It highlights that “optical field” problems in scattering media are typically formulated in terms of complex amplitudes, not only binary intensity patterns. The reviewed paper’s setup is explicitly amplitude-to-amplitude with binary modulation and intensity speckle capture, which is a different and more restricted measurement model. Therefore, the manuscript’s wording “arbitrary optical fields” risks conflating a binary amplitude communication task with broader complex-field transmission/control tasks. This matters because the claimed significance depends on breadth of applicability. The paper should either justify why its demonstrated setting suffices for “arbitrary optical fields” or narrow the claim.\n“We use Deep Neural Networks (DNNs) to classify and reconstruct a large database of handwritten digits from the intensity of the speckle patterns that result after the images propagated through multimode fibers (MMF).” [2](#ref2)\nThis prior work explicitly frames the deep learning task as reconstructing images from intensity-only speckle patterns, which is closely aligned with the reviewed paper’s measurement model. It also implicitly scopes the reconstruction target to intensity images (e.g., handwritten digits) rather than arbitrary complex optical fields. By comparison, the reviewed manuscript’s abstract elevates the claim to “arbitrary optical fields,” which is broader than what intensity-only speckle inversion typically supports without additional assumptions or measurements. The quote helps contextualize what is commonly demonstrated in deep-learning-based MMF image reconstruction: intensity image recovery under certain conditions. It therefore underscores that the reviewed paper’s experimental evidence (binary amplitude patterns and intensity speckle) supports a narrower claim than stated. This discrepancy weakens the conclusions’ generality.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|64|GPT|5", "source": "prb", "split": "test", "paper_id": "prb64", "comment": "The paper’s conclusion that MMDN provides a “comprehensive improvement” and robust long-term operation is not sufficiently supported by the comparison design, which uses a limited static-network baseline and omits comparisons to established strategies that explicitly address dynamic/perturbed MMF transmission.\n\n“The static neural network (StaticNN) trained on the first 500-second data and tested on the following 500-second is taken as the baseline method. The MMDN was dynamically updated at each 5-second interval.”\nThis comparison contrasts an updating method against a non-updating method, so it primarily demonstrates that online adaptation can help under drift—something that is plausible but not, by itself, evidence of broad superiority over alternative dynamic-handling strategies. In dynamic MMF settings, common baselines include models trained to generalize across perturbations, periodic recalibration strategies, or adaptive synthesis approaches; without such comparisons, it is difficult to attribute gains specifically to the proposed multi-timescale memory ensemble design. Additionally, training StaticNN for 500 seconds and then freezing it is a particular baseline choice; other static baselines (e.g., shorter, more recent training windows) could be closer to the current channel state and reduce the apparent advantage. Because the paper claims near-perfect performance over long durations, conclusions depend on whether MMDN’s advantage persists against stronger baselines, not just a single frozen model. The manuscript does not report such comparisons, limiting the robustness of its conclusions. This affects perceived significance and the strength of evidence for the stated claims.\n“We compared MMDN with previous approaches in terms of time duration, reconstruction quality, and transmission distance, etc., and demonstrated a comprehensive improvement of our approach (see Supplementary Fig. 7).”\nThe manuscript asserts a comprehensive improvement over “previous approaches,” but the main paper’s quantitative comparisons presented in the provided text focus on StaticNN versus MMDN. Without explicit head-to-head evaluation against representative prior dynamic methods under matched conditions, the strength of this claim cannot be assessed from the main document. This is particularly important because the field contains methods tailored to perturbations (e.g., training across multiple conformations) that may offer robustness without online label-dependent tuning. A reader needs transparent details of which baselines were implemented, their hyperparameters, and how their data regimes match MMDN’s. Referring to an external supplementary figure without providing the methodological comparison details in the main text reduces verifiability of the “comprehensive improvement” conclusion. As a result, the conclusion appears stronger than what the disclosed evidence supports.\n“To overcome this challenge, a deep learning approach that generalizes over mechanical perturbations is presented.” [1](#ref1)\nThis sentence highlights an established alternative framing for dynamic MMF channels: training a model to generalize across perturbations rather than relying on online self-updating. Because the reviewed paper’s main experimental baseline is a frozen static model, it does not directly test whether MMDN outperforms a generalization-trained approach on comparable perturbation/drift conditions. Including such a baseline is important to substantiate novelty and superiority claims, since both directions (generalization across perturbations vs. online adaptation) aim to handle channel variability. Without direct comparison, the manuscript’s claim of comprehensive improvement over prior work is not convincingly supported by the presented evidence. This does not negate the possibility that MMDN is better, but it means the conclusion is not robustly demonstrated. Therefore, the paper’s comparative claims are currently under-evidenced.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|64|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb64", "comment": "The paper claims to use a \"self-supervised\" method where the model is updated using \"predicted input images as labels\". However, the implementation uses ground truth labels (`y_fortest`) for validation and early stopping during the online adaptation phase. This invalidates the claim of self-supervision as it relies on ground truth information that would not be available in a real deployment scenario.\n\n\"The MMDN model will be dynamically updated by online training on the unlabeled streaming data using predicted input images as labels, hence working in a self-supervised architecture.\"\nThe authors explicitly claim that the method is self-supervised and uses predicted labels for training. This implies that no ground truth is needed during the adaptation phase.\n```python\nclf1.fit(x_labeled[-int(sizeOfPretrain/3*2):], y_labeled[-int(sizeOfPretrain/3*2):], batch_size=batch_size, epochs=int(2*epochs), callbacks=get_callbacks(), validation_data=(x_fortest, y_fortest))\n```\nIn `code/MMDN.py`, the `fit` function is called with `validation_data=(x_fortest, y_fortest)`. `y_fortest` contains the ground truth labels for the current batch. This shows that the training process has access to the ground truth for validation.\n```python\ndef get_callbacks():\n    early_stopping = EarlyStopping(monitor='val_loss', min_delta=5e-6, patience=10, verbose=2, mode='min') # min_delta=5e-6\n    csv_logger = CSVLogger('./log.csv', append=True)\n    tensorboard = TensorBoard(log_dir='./logs', histogram_freq=0, write_graph=False)\n    return [tensorboard, csv_logger, early_stopping]\n```\nIn `code/model.py`, the `get_callbacks` function defines an `EarlyStopping` callback that monitors `val_loss`. Since `val_loss` is calculated using the ground truth `y_fortest` passed in `fit`, the model uses ground truth to decide when to stop training. This optimization based on ground truth is not possible in a true self-supervised setting and constitutes a significant methodological flaw (data leakage).", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|64|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb64", "comment": "The paper claims \"high-fidelity transmission of arbitrary optical fields\", but the experiments are limited to low-resolution (32x32) binary patterns. This resolution is significantly lower than standard image transmission benchmarks (e.g., 128x128 or higher grayscale/color images) and does not demonstrate the capability to transmit \"arbitrary\" fields, especially complex-valued or high-resolution natural scenes.\n\n\"We demonstrate >99.9% accuracy in the transmission of 1024 spatial degree-of-freedom... The long-term high-fidelity capability enables compressive encoded transfer of high-resolution video...\"\nThe claim of \"high-fidelity\" is based on the transmission of 1024 pixels (32x32 resolution). While the bit error rate is low (>99.9% accuracy), calling 32x32 binary transmission \"high-fidelity\" is misleading in the context of imaging, where high fidelity usually implies high resolution and accurate intensity/phase reconstruction.\n\"Our research employed arbitrary random binary images... The input images tested in the experiments are of 16×16-pixel and 32×32-pixel resolution.\"\nThe experiments are restricted to 32x32 binary patterns. This contradicts the abstract's broad claim of transmitting \"arbitrary optical fields\", as binary patterns are a specific and easier subset of arbitrary fields (which include grayscale and complex-valued fields).\n\"We used a binary SLM as the amplitude modulator to encode the spatial information...\"\nThe use of a binary SLM further confirms that the system is designed for and tested on binary data. The ability to transmit binary data does not automatically generalize to \"arbitrary optical fields\" with continuous amplitude and phase.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|64|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb64", "comment": "The proposed self-training method relies on pseudo-labels generated by the model itself. The paper does not adequately address the risk of error accumulation (model collapse) in the absence of ground truth (assuming the leakage issue is fixed). The confidence metric used is simplistic (based on binarization) and may not prevent confident errors, leading to confirmation bias.\n\n\"The network parameters are dynamically updated over time in a self-supervised manner, by learning from currently predicted pseudo-labels to synthesize the optimal inverse transmission model...\"\nThe method relies on its own predictions to update the model. This creates a feedback loop where errors can be reinforced. The paper does not provide theoretical or empirical analysis on how the method prevents model collapse, a common failure mode in self-training (as discussed in TENT [1] and SHOT [2]).\n```python\ndef confidenceFactor(arr):\n    median = 0.5\n    confList = []\n    for i in range(0, arr.shape[0]):\n        conf = np.sum(np.abs(arr[i] - median)*1.8 + 0.1) / arr.shape[-1]\n        confList.append(conf)\n    meanConf = np.mean(confList)\n    return confList, meanConf\n```\nIn `code/model_cotrain.py`, the confidence metric is calculated based on the distance from 0.5. This measures how \"binary\" the output is, not how correct it is. A model can be confidently wrong (e.g., predicting a perfect \"1\" when the true label is \"0\"), especially under severe channel distortions. Using this metric to weight the ensemble does not guarantee robustness against error propagation.\n\nReferences:\n[1] Wang, Dequan, et al. \"Tent: Fully test-time adaptation by entropy minimization.\" International Conference on Learning Representations (2021). https://openreview.net/forum?id=uXl3bZLkr3c\n[2] Liang, Jian, et al. \"Do we really need to access the source data? Source hypothesis transfer for unsupervised domain adaptation.\" International Conference on Machine Learning (2020). https://proceedings.mlr.press/v119/liang20a.html", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|64|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb64", "comment": "The paper only compares the proposed method with a static neural network baseline. It does not compare with other adaptive methods or state-of-the-art MMF transmission techniques, such as those using physics-based constraints or other test-time adaptation strategies.\n\n\"The static neural network (StaticNN) trained on the first 500-second data and tested on the following 500-second is taken as the baseline method.\"\nThe comparison is limited to a static baseline, which is known to fail in dynamic environments. This sets a weak baseline.\n\"Image transmission through a dynamically perturbed multimode fiber by deep learning [3]\"\nThe paper cites Resisi et al. [3] which proposes a deep learning approach for dynamically perturbed MMFs. However, it does not compare the proposed method against this relevant competitor.\n\"Adaptive 3D descattering with a dynamic synthesis network [4]\"\nThe paper cites Tahir et al. [4] which also addresses adaptive descattering. A comparison with such dynamic methods is necessary to demonstrate the significance of the proposed approach.\n\nReferences:\n[3] Resisi, Shachar, et al. \"Image transmission through a dynamically perturbed multimode fiber by deep learning.\" Laser & Photonics Reviews 15.10 (2021): 2000553. https://onlinelibrary.wiley.com/doi/full/10.1002/lpor.202000553\n[4] Tahir, Waleed, et al. \"Adaptive 3D descattering with a dynamic synthesis network.\" Light: Science & Applications 11.1 (2022): 42. https://www.nature.com/articles/s41377-022-00716-6", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|64|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb64", "comment": "As a dynamic neural network, the update mechanism was hardly explained in the manuscript. How does the proposed CNN update its memory by its input sequence? What is the difference between S1, S2, and L3? What is the updating frequency for these three modules?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|64|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb64", "comment": "In addition to the static neural network baseline, I also wonder how conventional algorithms would perform against the reported method. Benchmarking would be good to include.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|64|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb64", "comment": "The specs of the MMF used in the experiment are not listed.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|64|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb64", "comment": "In line 219, please give a reference to AdaDelta paper.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|64|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb64", "comment": "The number of trainable parameters, and the training time on the given machine are not mentioned in the Methods section.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|64|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb64", "comment": "For Fig. 1b, the pink texts on the left, what is “self-s update”?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|64|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb64", "comment": "Could the authors explain why they design a multi-memory network with two branches representing interleaved short-term modeling and one branch for long-term modeling, instead of one short-term and one-long-term structure?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|64|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb64", "comment": "Could the author discuss more on the choice of self-supervised model updating interval? Is it relevant to the MMF characteristics only or also affected by other factors (e.g., imaging rate)?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|64|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb64", "comment": "What is the beam size of the incident light on the SLM and onto the entrance of the MMF? The authors have experimented on MMFs with different diameters. Is the beam size the same in all experiments and does the fill factor influence on the transmission performance?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|64|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb64", "comment": "I would suggest the authors to provide their code to facilitate the audience.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|64|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb64", "comment": "Would this work be of significance to the field? Currently shown evidence is not sufficiently convincing. A comparison with single-mode fiber (SMF), which is widely used in optical communication, could further underscore the significance of your findings. Evaluating the potential benefits of integrating the MMDN with MMFs in contrast to SMFs would be insightful. Specifically, if the SLM or DMD's speed is limited to certain kHz, how would the bandwidth of MMFs compare with that of SMFs?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|64|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb64", "comment": "Needs more convincing demos than binary input. While the video streaming experiment has been demonstrated to showcase its potentials to optical telecommunications, its impact on other applications such as remote sensing and endoscopy is unclear to me. It seems to me that MMDN is designed for decoding binary input patterns, while the images obtained in remote sensing and endoscopy are normally non-binary. Besides, MMDN requires real-time model correction via inspecting images at the distal end, which is arguably only possible with some types of “guidestars” as a feedback signal and thus substantially restricts its use scenario. On the other hand, data streaming via binary pattern decoding limits the operation of MMF at its maximum possible throughput, where a continuous level (or at least gray level) streaming is available. To validate its broad impact and applicability, it would be valuable to see some non-binary decoding results. Also, discussions on some real-world scenarios in which MMDN is viable would be helpful.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|64|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb64", "comment": "Needs more clarity on how it works. The primary merit of MMDN is its self-supervised adaptive learning capability. However, how the online learning works is neither elucidated in detail nor accompanied with proper reference. Without knowing the exact working principle and how the unseen unlabeled data are utilized to update the model, it is not clear whether MMDN serves as an efficient solution to perturbation-robust data transmission in MMFs.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|64|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb64", "comment": "Another concern is the amount of training data required for the initial model and each model update. First, 20,000 paired data for the initial model are not viable in most of the real applications in remote sensing and endoscopy even in a static system, which is probably even more challenging in a dynamic system as considered in the manuscript. In addition, it’s not clearly stated in the manuscript how many patterns are needed for each update. Given the relatively small number of input modes and the development of efficient calibration methods (e.g., Li, S., Saunders, C., Lum, D.J. et al. Compressively sampling the optical transmission matrix of a multimode fibre. Light Sci Appl 10, 88 (2021).), if the number of patterns is comparable to the number of input modes, MMDN might not provide an edge on calibration efficiency, i.e., the number of data acquisitions required for each calibration. It would be useful to include more demonstration and discussion on the possibility of using a smaller training dataset and its calibration efficiency compared to conventional methods such as transmission-matrix-based method.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|64|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb64", "comment": "The statement \"We experimented on an amplitude-to-amplitude optical setup\" requires clarification.\n\ni. Is \"amplitude-to-amplitude\" synonymous with \"intensity-to-intensity\"?\n\nii. How does the SLM plane relate to the fiber input plane? Is the SLM on the Fourier plane of the objective lens, and are these two planes conjugate or Fourier related?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|64|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb64", "comment": "The characterization of the MMFs as \"highly variable\" in the experiment involving two different MMF channels needs to be better defined. As per Supplementary Figure 2, these MMF channels seem to fall under \"medium instability\".", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|65|Claude|3", "source": "prb", "split": "test", "paper_id": "prb65", "comment": "While the paper presents simulated Strehl ratios and MTFs, there is no quantitative comparison of these simulated optical performance metrics with experimentally measured values, limiting the ability to assess the accuracy of the design framework.\n\n\"In our simulations, the optimized broadband meta-optics displayed significantly larger wavelength-averaged Strehl Ratios—0.045 for the meta-optics with 'complex' scatterers and 0.018 for those with 'simple' scatterers, as compared to 0.0075 for the forward-designed hyperboloid metalens.\"\nThese simulated Strehl ratio values are reported, but the paper does not provide corresponding experimentally measured Strehl ratios from the fabricated devices. The supplementary materials show qualitative PSF and MTF comparisons (Fig. S2, S3), but no numerical Strehl ratio values are extracted from experimental measurements. In meta-optics research, it is standard practice to quantitatively compare simulated and measured optical performance [[3]](#citation-list), as fabrication imperfections often lead to significant performance degradation.\n* Quote from Supplementary: \"The experimental results displayed a strong correlation with the simulations, underlining the accuracy and reliability of our computational models.\"\nThis claim of \"strong correlation\" is qualitative and not supported by numerical comparison. Prior work in meta-optics has demonstrated that measured focusing efficiencies and Strehl ratios can deviate substantially from simulations due to fabrication errors, and such discrepancies require quantitative characterization [[4]](#citation-list). Without numerical comparison of simulated versus measured Strehl ratios, the claimed accuracy of the design framework remains unverified.\n\nReferences:\n[3] [Nanoscale precision brings experimental metalens efficiencies on par with theory - Nature Communications Physics](https://www.nature.com/articles/s42005-024-01598-6)\n[4] [All-Glass 100 mm Diameter Visible Metalens for Imaging the Cosmos - ACS Nano](https://pubs.acs.org/doi/10.1021/acsnano.3c09462)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|65|Claude|4", "source": "prb", "split": "test", "paper_id": "prb65", "comment": "The paper contains an internal inconsistency regarding the number of wavelengths used in optimization: the main text states 8 wavelengths while the Methods section states 13 wavelengths. Additionally, regardless of which number is correct, the sparse wavelength sampling results in suboptimal performance at intermediate wavelengths.\n\n* Quote from main text: \"The simulations were, however, limited to 8 optimized wavelengths spanning from 8 to 12 μm due to memory constraints.\"\nThis statement indicates that only 8 discrete wavelengths were used for optimization across the 4 μm LWIR bandwidth, with the sampling interval being approximately 0.57 μm.\n* Quote from Methods section: \"During optimization, a total of 13 samples of wavelengths are used uniformly spanning from 8μm to 12μm.\"\nThis contradicts the main text, which states 8 wavelengths. The discrepancy between \"8 optimized wavelengths\" in the results and \"13 samples of wavelengths\" in the Methods creates confusion about the actual experimental conditions. This inconsistency should be reconciled for reproducibility. Furthermore, regardless of whether 8 or 13 wavelengths were used, the authors acknowledge that \"the spectral regions between the sampled wavelengths exhibit relatively lower Strehl ratios compared to the peak values,\" confirming that the discrete optimization approach yields non-uniform spectral performance.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|65|Claude|5", "source": "prb", "split": "test", "paper_id": "prb65", "comment": "The paper acknowledges using the local phase approximation (LPA), which is known to have reduced accuracy for high phase gradients, but does not quantify how this approximation affects the accuracy of the design predictions for the large-aperture, relatively high-NA (0.45) meta-optics presented.\n\n\"Also, our design currently relies on the local phase approximation, which is known to provide lower efficiency for meta-optics.\"\nThe LPA treats each meta-atom as if it were in an infinite periodic array, ignoring coupling effects between adjacent dissimilar meta-atoms. This approximation becomes increasingly inaccurate when the phase profile has large gradients, which occur in high-NA and large-aperture designs. Research has shown that \"local approximations based on periodic boundary conditions ignore the gradient coupling effect in the actual arrangement of meta-atoms, leading to a mismatch between the ideal and actual devices\" [[5]](#citation-list). For the NA=0.45 design in this paper, the phase gradient at the lens edge can be substantial, yet no analysis is provided of how LPA inaccuracy affects the predicted versus actual optical performance.\n\"However, recently a physics-inspired neural network has been used to design meta-optics without making such approximation and can be readily adapted for the scatterer-to-field mapping.\"\nWhile the authors reference alternative methods that avoid the LPA, they do not implement them or compare results. Other recent works have demonstrated that accounting for near-field coupling can significantly affect design accuracy, particularly for metalenses with centimeter-scale apertures [[6]](#citation-list). The impact of the LPA on the six-fold Strehl ratio improvement claim remains uncharacterized.\n\nReferences:\n[5] [Physics-data-driven intelligent optimization for large-aperture metalenses - Opto-Electronic Advances](https://www.oejournal.org/oea/cn/article/pdf/preview/10.29026/oea.2023.230133.pdf)\n[6] [AI for optical metasurface - MIT Web](http://web.mit.edu/hujuejun/www/My%20Papers/Journal%20Papers/AI%20for%20optical%20metasurface.pdf)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|65|GPT|1", "source": "prb", "split": "test", "paper_id": "prb65", "comment": "This paper makes an inaccurate quantitative claim (Validity, Conclusions) that the “simple scatterers” meta-optic achieves higher PSNR than the hyperboloid baseline in the in-lab broadband/narrowband imaging comparison, but the supplementary PSNR table reports lower PSNR for the simple-scatterer design in key conditions, undermining the reliability of the stated comparative conclusion.\n\n“Additionally, the MTF-engineered meta-optic with simple scatterers demonstrates superior performance over the forward-designed hyperboloid metalens, as evidenced by a clearer image and higher peak signal-to-noise ratio (PSNR) for both patterns in both the 10 \\( \\mu \\)m and 12 \\( \\mu \\)m cases.”\nThis sentence asserts a specific quantitative relationship (“higher PSNR”) and uses it as evidence for a performance conclusion. Because PSNR is an objective metric, this claim can be directly checked against the paper’s own reported PSNR values. If the reported PSNR values do not support the stated inequality, then the interpretation of the imaging experiment is not internally consistent. In computational/imaging papers, such internal inconsistencies are significant because they call into question whether the comparison was summarized correctly or whether additional (unstated) processing choices affected the numbers. The issue is not about small effect sizes; it is about the direction of the reported metric relative to the claim. As a result, the conclusion that the “simple scatterers” design clearly outperforms the hyperboloid baseline is not robust as written.\n“Table 1 Peak Signal-to-Noise Ratio in dB”\nThe supplementary material explicitly frames Table 1 as the quantitative comparison supporting claims about image quality. Since the table is presented as the definitive PSNR report for the exact experimental conditions (broadband, 10 µm bandpass, 12 µm bandpass), discrepancies between the narrative and the table materially affect the credibility of the results section. In imaging evaluations, PSNR is sensitive to registration, tone mapping, and preprocessing; therefore, papers typically ensure the narrative aligns precisely with the reported values. Here, the table is the authoritative numerical record, so any mismatch indicates either an error in the text or in the metric computation/reporting. Either case directly impacts the soundness of the conclusions drawn from Fig. 3. This is a major issue because the paper uses PSNR to argue superiority of one optical design over another.\n“<table>\n  <tr>\n    <th></th>\n    <th>Hyperboloid</th>\n    <th>Simple</th>\n    <th>Complex</th>\n  </tr>\n  <tr>\n    <td>Broadband</td>\n    <td>11.49</td>\n    <td>10.84</td>\n    <td>13.33</td>\n  </tr>\n  <tr>\n    <td>Narrow-band 10 µm</td>\n    <td>10.74</td>\n    <td>9.38</td>\n    <td>10.67</td>\n  </tr>\n  <tr>\n    <td>Narrow-band 12 µm</td>\n    <td>8.26</td>\n    <td>10.02</td>\n    <td>12.65</td>\n  </tr>\n</table>”\nThese reported PSNR values contradict the main-text claim that the simple-scatterer meta-optic has “higher PSNR” than the hyperboloid “for both patterns” in the 10 µm and 12 µm cases. Specifically, at broadband the simple design (10.84 dB) is lower than hyperboloid (11.49 dB), and at narrow-band 10 µm the simple design (9.38 dB) is lower than hyperboloid (10.74 dB). Only in the 12 µm condition does the simple design exceed the hyperboloid baseline (10.02 dB vs 8.26 dB). Because the claim asserts higher PSNR in both the 10 µm and 12 µm cases, the 10 µm row alone falsifies the statement as written. This is not a minor reporting issue: it changes which design appears better under at least one experimentally emphasized condition. Consequently, the comparative conclusion about simple-scatterer performance relative to the hyperboloid baseline is not supported by the paper’s own quantitative evidence.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|65|GPT|2", "source": "prb", "split": "test", "paper_id": "prb65", "comment": "This paper’s central broadband-imaging claim (Validity, Conclusions) is insufficiently validated experimentally because the PSF/MTF characterization is sparsely sampled over 8.0–10.5 µm, explicitly avoids the optimized wavelengths, and uses a laser source limited to 8.23–10.93 µm, leaving the upper portion of the stated 8–12 µm band (including the demonstrated 12 µm filtered imaging) without direct PSF/MTF measurement evidence.\n\n“Here, we employ inverse-design to create broadband meta-optics operating in the long-wave infrared (LWIR) regime (8-12 \\( \\mu \\)m).”\nThis sentence defines the claimed operational bandwidth, which is central to the paper’s novelty and its performance claims. When a work claims broadband imaging across a specific spectral interval, common practice is to provide experimental optical characterization (e.g., PSF/MTF, focal shift, efficiency) that spans the full interval or clearly justifies extrapolation. Because chromatic aberrations and dispersion effects are wavelength-dependent, partial-band measurements can miss failure modes near band edges. The bandwidth claim is used to motivate both the inverse-design method and the comparison to a chromatic hyperboloid baseline. Therefore, the adequacy of the experimental validation must be judged relative to the full 8–12 µm interval stated here. Without full-band PSF/MTF characterization, the paper’s conclusions about uniform performance over 8–12 µm are not fully supported.\n“These measurements were taken in light of the alignment sensitivity explained in Section S1, necessitating sparse sampling of PSFs across the spectrum at specific wavelengths—namely, 8.0, 8.5, 9.5, 10.0, and 10.5 micrometers.”\nThis explicitly limits the experimental PSF sampling to five wavelengths and, importantly, only up to 10.5 µm. Even if sparse sampling is acceptable for a preliminary check, it still needs to cover the claimed band edges (especially near 12 µm) to validate broadband performance claims. The stated sampling omits the 11–12 µm region where the paper also presents narrowband 12 µm imaging results, which are used to argue broadband capability. Moreover, sparse sampling increases the risk that unmeasured spectral regions have significantly different PSF structure (e.g., larger sidelobes or defocus) that would affect both MTF and deconvolution quality. In broadband diffractive/meta-optics, band-edge behavior is often where performance degrades most. As a result, the limited wavelength set is not sufficient evidence for the full 8–12 µm claim.\n“It is important to note that due to the aforementioned alignment sensitivity (as discussed in Section S1), we deliberately refrained from capturing PSFs at the optimized wavelengths.”\nThis sentence is particularly problematic because it states that PSF measurements were not taken at the very wavelengths used to optimize the meta-optic. If optimized-wavelength performance is not experimentally measured, the paper cannot directly validate the primary design objective on the wavelengths that define the figure of merit. While alignment sensitivity is a real experimental concern, avoiding optimized wavelengths creates a validation gap: the strongest expected performance points are not measured, and model agreement is tested only off-target. In optics and computational imaging, it is common to address alignment sensitivity by reporting alignment tolerances, measuring multiple repeats, or jointly estimating a small number of alignment parameters during PSF fitting—rather than omitting the critical wavelengths entirely. The omission weakens the link between the optimization claim and the experimental confirmation. Therefore, the experimental evidence does not adequately corroborate the broadband optimization objective.\n“• Laser Source: 8.23 - 10.93 µm QCL”\nThis line shows that the characterization source does not cover the full 8–12 µm interval claimed in the main paper. In particular, it cannot reach 12 µm, yet the main paper emphasizes imaging with a 12 µm bandpass filter and discusses performance across the full LWIR band. Without an experimental source spanning the full band, the paper must rely on simulations or indirect evidence for the missing wavelengths, which should be clearly stated and quantified. The mismatch between claimed bandwidth and characterization bandwidth is a significant methodological gap because the PSF/MTF is the key physical quantity used both for interpreting optical performance and for computational deconvolution. Given known fundamental bandwidth limits in achromatic metalenses, complete spectral validation is especially important [[4]](#ref4). As written, the experimental characterization does not directly support the full-band conclusions.\n“Here, we derive fundamental bandwidth limits that apply to broadband optical metalenses, regardless of their implementation.” [[4]](#ref4)\nThis literature statement underscores that broadband metalens performance is constrained by physical bandwidth-delay limits, motivating careful full-band validation rather than extrapolation from partial measurements. Because such limits often manifest most strongly at band edges, missing measurements near 11–12 µm leaves open whether the proposed meta-optic approaches the claimed broadband behavior there. In other words, the field’s prior work suggests that broadband claims require comprehensive spectral evidence to be credible. This does not refute the possibility that the device works at 12 µm, but it raises the evidentiary standard for the paper’s broad claims. The paper’s partial-band and off-optimized-wavelength characterization falls short of that standard. Consequently, the conclusions about broadband performance across 8–12 µm are not fully justified by the presented experimental data.\n\nReferences:\n[4] [F. Presutti, F. Monticone, “Focusing on Bandwidth: Achromatic Metalens Limits” (arXiv:2001.10899)](https://arxiv.org/abs/2001.10899)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|65|GPT|3", "source": "prb", "split": "test", "paper_id": "prb65", "comment": "This paper has major reproducibility weaknesses (Data and methodology) because key optimization specifications are inconsistent across sections and the accompanying code implements a different MTF/Strehl-style metric than the paper’s equations, making it unclear what exact objective produced the reported “Strehl ratio” and FoM values.\n\n“The simulations were, however, limited to 8 optimized wavelengths spanning from 8 to 12 μm due to memory constraints.”\nThis sentence specifies a concrete experimental-design choice: the number of wavelengths used in simulation/optimization (8). Because the paper’s central claim is broadband performance, the set of wavelengths used in optimization directly affects both the achieved performance and the interpretation of “wavelength-averaged” metrics. In inverse design for broadband optics, the wavelength sampling strategy (count, spacing, weighting) is critical and is typically reported consistently across the paper. Any ambiguity here makes it difficult to reproduce the optimization and to understand how performance between sampled wavelengths should behave. Moreover, memory constraints often imply approximations that should be clearly documented, since they can bias performance toward sampled points. Therefore, this statement must align with the Methods section to support reproducibility.\n“During optimization, a total of 13 samples of wavelengths are used uniformly spanning from 8\\( \\mu \\)m to 12\\( \\mu \\)m.”\nThis directly contradicts the earlier statement that simulations were limited to 8 optimized wavelengths. A difference between 8 and 13 wavelength samples is not a trivial reporting discrepancy; it changes the effective objective, gradient contributions, and the meaning of “uniform performance” across the band. If 13 wavelengths were used in the optimization loop, then the statement about being “limited to 8 optimized wavelengths” needs clarification (e.g., 8 for reporting Strehl plots vs 13 for FoM). Without such clarification, an independent researcher cannot replicate the optimization setup or fairly compare computational costs. In broadband metasurface optimization, the number of wavelength samples is often one of the dominant runtime factors, so the inconsistency is also material for feasibility claims. This inconsistency undermines the transparency of the methodology.\n“The DNN surrogate model uses four layers of fully connected layers that have 256 units and hyperboloid tangent as the activation function for each layer.”\nThis provides a specific neural surrogate architecture, which is a critical component of the claimed “deep-learning assisted” differentiable pipeline. Reproducing the surrogate requires knowing the exact architecture, activation functions, optimizer settings, and training data generation. In the context of meta-atom surrogate modeling, architectural choices can strongly affect generalization across wavelength and geometry, which in turn affects the meta-optic optimization outcome. Therefore, these details should be consistent with the supplementary “Meta-atom Modeling” section that reports training settings and losses. If the surrogate architecture differs across sections, it is unclear which model produced the reported designs. This creates ambiguity about whether the surrogate performance claims (e.g., “strong correlation” with simulations) are attributable to the specified network. Such ambiguity is a major obstacle to reproducibility.\n“The models were trained using a 10-layer fully connected network (FCC) with 128 units per hidden layer and a ReLU activation function. Both models were trained using the Adam optimizer, with a learning rate set at 0.0006.”\nThis supplementary description conflicts with the Methods description of a 4-layer, 256-unit, tanh network and a learning rate of \\(10^{-3}\\). These differences (depth, width, activation, learning rate) are substantial and would plausibly change surrogate accuracy and optimization behavior. In surrogate-based inverse design, the surrogate error can translate directly into systematic errors in the optimized optic (e.g., incorrect phase/dispersion predictions), so reporting the correct model is important for assessing validity. Without a reconciliation (e.g., different networks for different scatterer classes or a later revision), the reader cannot determine which surrogate was actually used. This inconsistency also complicates interpretation of Fig. S7 training losses, since the architecture that generated those curves is unclear relative to the main text. Overall, the surrogate modeling component is insufficiently specified in a self-consistent way.\n“The normalized MTF is defined as \\( \\hat{M} = M(k_x, k_y, \\lambda)/D(k_x, k_y, \\lambda) \\).”\nThis equation defines the normalization central to the paper’s “modified Strehl ratio” and its interpretation as a volume under a normalized MTF surface. If the metric is normalized pointwise by the diffraction-limited MTF \\(D\\), then the resulting integral has a specific physical meaning: it measures how close the system’s OTF/MTF is to the diffraction-limited case across spatial frequencies. Many optics papers are careful about this normalization because different normalizations (e.g., peak-normalization vs diffraction-limited normalization) yield different numerical values and different optimization incentives. Therefore, the implementation used to compute the reported Strehl/FoM should match this definition. If the released code uses a different normalization, reproducing the reported numbers and comparisons becomes ambiguous. This is particularly important because the paper reports specific wavelength-averaged Strehl values (e.g., 0.045, 0.018, 0.0075).\n```python\ndef get_mtf_volume(field: propagation.Field2D, use_log: bool = False) -> tf.Tensor:\n    psf_tensor = field.get_intensity()\n    norm_factor = tf.reduce_sum(psf_tensor, axis=[-2, -1], keepdims=True)\n    norm_factor = tf.reshape(norm_factor, [len(field.wavelength), -1, 1, 1])\n    norm_psf = psf_tensor / norm_factor\n    norm_psf = tf.cast(norm_psf, dtype=tf.complex64)\n\n    mtf = tf.abs(tf.signal.fftshift(tf.signal.fft2d(norm_psf)))\n    mtf_max = tf.math.reduce_max(mtf, axis=[-1, -2])\n    mtf_max = tf.reshape(mtf_max, [len(field.wavelength), -1, 1, 1])\n    mtf_norm = mtf / mtf_max\n\n    volume = tf.math.reduce_mean(mtf_norm, axis=[-1, -2])\n\n    if use_log:\n        volume = tf.math.log(volume)\n        volume = tf.math.reduce_mean(volume)\n\n    return volume\n```\nThis code computes an “MTF volume” by normalizing the MTF by its own maximum (peak-normalization) and then averaging across spatial frequencies. That differs from the paper’s stated pointwise normalization by the diffraction-limited MTF \\(D(k_x,k_y,\\lambda)\\), and it also does not explicitly restrict the integration/average to the diffraction cutoff region \\([-k_{x1},k_{x1}]\\times[-k_{y1},k_{y1}]\\) described in the paper. While peak-normalization can be a reasonable heuristic, it changes the metric’s meaning and the optimization landscape relative to a diffraction-limited normalization. Because the paper’s reported “Strehl ratio” values are central to its headline “six-fold improvement” claim, it matters whether those numbers come from the paper’s definition or from a different implementation. The presence of a released implementation with a different normalization makes it unclear which metric underlies the results. This ambiguity materially hinders independent reproduction and verification.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|65|GPT|4", "source": "prb", "split": "test", "paper_id": "prb65", "comment": "This paper’s real-world imaging conclusions (Conclusions; Appropriate use of statistics and treatment of uncertainties) are not robust because the “in-the-wild” comparisons are based on a semi-blind deconvolution that jointly estimates the image, PSF, and fixed-pattern noise from a single capture per scene, with primarily qualitative assessment and limited reporting of constraints/hyperparameters, making it difficult to rule out reconstruction artifacts or non-uniqueness.\n\n“In each case, we captured a single image using a FLIR A65 sensor, and performed a numerical deconvolution (details in the Methods and supplementary information).”\nA single-capture demonstration provides limited evidence for robustness, especially when the post-processing includes solving an inverse problem that can be sensitive to initialization and regularization. In imaging, reporting multiple trials (or at least sensitivity to hyperparameters) is a common way to separate repeatable improvements from incidental reconstructions. Because the scenes are uncontrolled (“in the wild”), sensor noise, temperature gradients, and alignment can vary substantially, and a one-off result can be cherry-picked unintentionally. This sentence also makes clear that the key qualitative comparisons in Fig. 4 depend on the deconvolution pipeline, not only on the optical PSF itself. Therefore, the claim that the MTF-engineered meta-optic “clearly” recovers sharper real-world details is difficult to validate without repeated trials or uncertainty reporting. As written, the evidence base for the in-the-wild conclusion is too thin.\n“We perform a semi-blind deconvolution where we initialize \\(K\\) to be the analytical PSF from our simulations, and then solve for the parameters of the network and the PSF together.”\nJointly estimating the sharp image and the PSF from a single degraded observation is a classic ill-posed problem, and allowing the PSF to change during optimization can absorb modeling errors in ways that may not correspond to the physical optics. Without explicit constraints on \\(K\\) (e.g., non-negativity, normalization, support constraints, parametric forms) and without reporting how strongly \\(K\\) is regularized, the reconstruction can trade off between sharpening the image and modifying the PSF. This matters because the paper’s optical claim is about improving the physical MTF/PSF; a flexible semi-blind deconvolution can partially “manufacture” apparent sharpness. In computational photography and computational imaging, semi-blind deconvolution pipelines are typically validated by synthetic tests with known ground truth or by reporting consistency across multiple frames. The paper does not provide such robustness checks for the in-the-wild scenes. Consequently, the post-processed results cannot be cleanly attributed to the meta-optic alone.\n“Blind deconvolution is an ubiquitous non-linear inverse problem in applications like wireless communications and image processing. This problem is generally ill-posed since signal identifiability is a key concern, …” [[3]](#ref3)\nThis literature statement highlights that blind/semi-blind deconvolution can be non-identifiable: multiple image–kernel pairs can explain the same observation. That directly bears on the paper’s decision to jointly optimize \\(N_\\theta\\) and \\(K\\) from a single measurement, because improvements in the reconstructed image do not necessarily imply the recovered \\(K\\) matches the true optical PSF. The risk is higher when only qualitative comparisons are shown, since visually plausible reconstructions can occur even when the kernel estimate is wrong. The paper’s formulation also includes additional degrees of freedom (fixed pattern noise \\(F\\)), increasing ambiguity further. Standard practice in ill-posed inverse problems is to include quantitative validation and explicit constraints to ensure physically meaningful solutions. Without those safeguards, the conclusions drawn from reconstructions are less reliable.\n“Wavelet Implicit neural REpresentation (WIRE) uses a continuous complex Gabor wavelet activation function that is well-known to be optimally concentrated in space-frequency and to have excellent biases for representing images.” [[2]](#ref2)\nThis sentence supports that the chosen INR architecture intentionally imposes an image-biased prior. While such a bias can be beneficial for regularizing inverse problems, it also means reconstructions can preferentially resemble “natural” images even when the measurement information is insufficient to uniquely determine fine details. In the paper’s context, this raises the possibility that some of the recovered high-frequency structures in Fig. 4 reflect the INR prior rather than the meta-optic’s true optical transfer function. This does not imply the method is invalid, but it does increase the need for quantitative, controlled validation (e.g., on test targets with known ground truth under outdoor conditions). The paper’s in-the-wild section lacks such validation and instead relies on visual inspection of a few scenes. Given the strong prior described here, that evidentiary standard is not adequate to support strong conclusions about real-world imaging performance.\n“Implicitly defined, continuous, differentiable signal representations parameterized by neural networks have emerged as a powerful paradigm, offering many possible benefits over conventional representations.” [[5]](#ref5)\nThis sentence provides context for why INR-based reconstructions can be compelling: the representation class is expressive and can fit complex signals from coordinate inputs. In the paper under review, this expressiveness is leveraged to represent an entire thermal image as a continuous function and to regularize deconvolution “data-free.” However, high expressiveness also increases the space of plausible solutions when the forward model (PSF, fixed-pattern noise) is uncertain, which is exactly the semi-blind setting used here. In such settings, it is standard to report additional checks (e.g., multiple random initializations, constraints on the kernel, or controlled-target experiments) to ensure the recovered detail is measurement-supported rather than representation-driven. The paper does not report these robustness checks for the in-the-wild reconstructions. Therefore, the use of an expressive INR strengthens (rather than weakens) the need for stronger uncertainty/robustness reporting.\n“In this paper, we show that, on the contrary, the structure of a generator network is sufficient to capture a great deal of low-level image statistics prior to learning.” [[1]](#ref1)\nThis “Deep Image Prior” result is widely cited to explain why untrained networks can act as powerful priors for image restoration: the architecture itself imposes regularization that can yield plausible-looking images. The paper under review leverages exactly this kind of architecture-induced bias (“data-free image prior”) to solve a semi-blind deconvolution. Therefore, the external literature implies that visually improved reconstructions can occur even without ground-truth supervision, and that such reconstructions must be interpreted carefully. When combined with kernel estimation (semi-blind \\(K\\)), the degrees of freedom increase, and the risk of producing plausible but incorrect details also increases. This strengthens the critique that the paper should provide stronger robustness evidence (e.g., sensitivity analyses, repeat captures, or target-based quantitative metrics) for in-the-wild results. Without that, the conclusions from the reconstructed scenes are not as reliable as the paper suggests.\n\nReferences:\n[1] [D. Ulyanov, A. Vedaldi, V. Lempitsky, “Deep Image Prior” (arXiv:1711.10925)](https://arxiv.org/abs/1711.10925)\n[2] [V. Saragadam, D. LeJeune, J. Tan, G. Balakrishnan, A. Veeraraghavan, R. Baraniuk, “WIRE: Wavelet Implicit Neural Representations” (arXiv:2301.05187)](https://arxiv.org/abs/2301.05187)\n[3] [C. E. Shin, M. Soltanolkotabi, “Fundamental Limits of Blind Deconvolution Part II: Sparsity-Ambiguity Trade-offs” (arXiv:1503.03184)](https://arxiv.org/abs/1503.03184)\n[5] [V. Sitzmann, J. Martel, A. Bergman, D. Lindell, G. Wetzstein, “Implicit Neural Representations with Periodic Activation Functions” (arXiv:2006.09661)](https://arxiv.org/abs/2006.09661)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|65|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb65", "comment": "The paper makes a factually incorrect claim that the MTF-engineered meta-optic with simple scatterers demonstrates superior performance over the forward-designed hyperboloid metalens at 10 μm, while the provided quantitative data shows the opposite.\n\n\"Additionally, the MTF-engineered meta-optic with simple scatterers demonstrates superior performance over the forward-designed hyperboloid metalens, as evidenced by a clearer image and higher peak signal-to-noise ratio (PSNR) for both patterns in both the 10 \\( \\mu \\)m and 12 \\( \\mu \\)m cases.\"\nThis statement from the main text explicitly claims superior performance (higher PSNR) for the simple scatterer design at 10 μm.\n\"Table 1 Peak Signal-to-Noise Ratio in dB ... Narrow-band 10 µm ... Hyperboloid: 10.74 ... Simple: 9.38\"\nThe data in Table 1 of the Supplementary Information clearly shows that the Hyperboloid metalens has a higher PSNR (10.74 dB) than the Simple scatterer design (9.38 dB) at 10 μm. This directly contradicts the claim made in the main text.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|65|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb65", "comment": "The paper lacks clarity regarding the specific computational processing applied to the experimental results presented in Figure 3, making it difficult to assess the standalone optical performance versus the computationally enhanced performance.\n\n\"Fig. 3 Broadband imaging results in the lab (after computation)...\"\nThe caption of Figure 3 states that the results are \"after computation,\" implying some form of post-processing.\n\"The resultant imaging outputs, which are presented without any denoising, are displayed at the bottom of each sub-figure in Fig. 3.\"\nThe main text states that the results are \"without any denoising,\" which contradicts the caption's \"after computation\" label or creates confusion about what \"computation\" entails (e.g., background subtraction vs. deconvolution).\n\"Through this predefined post-processing routine, we were able to improve the dynamic range and reduce microbolometer array artifacts.\"\nSection 4.4 mentions background subtracting, contrast stretching, and block-matching denoising. It is unclear if \"after computation\" in Fig. 3 refers to this routine or the \"simple computational backend\" (INR) mentioned elsewhere, or if the \"without any denoising\" claim applies to the specific sub-figures mentioned.", "reviewer_type": "ai", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|65|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb65", "comment": "One prominent consideration throughout the paper revolves around the accuracy of the PSF and Strehl Ratio calculation method.\n\n1a) A comparison between the designs in Fig. 1 and SEM images in Fig. 2b indicates a potential design-to-fabrication gap. The precision of the calculated transmission and phase delay via RCWA warrants clarification.\n\n1b) Considering that RCWA pertains to periodic structures, the PSF calculated using element-wise performance, as seen in [M. V. Zhelyeznyakov et al., \"Deep Learning to Accelerate Scatterer-to-Field Mapping for Inverse Design of Dielectric Metasurfaces,\" ACS Photonics, 2021], raises questions about its reliability.\n\n1c) the accuracy and experimental validation of the \"Shifted angular spectrum propagation\" method require discussion. To enhance the credibility of the optimization framework, it would be prudent for the authors to present measured Strehl ratios and compare them with the results depicted in Fig. 1d.", "reviewer_type": "human", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|65|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb65", "comment": "Other approaches, such as that presented by [S. Shrestha et al., \"Broadband achromatic dielectric metalenses,\" Light: Science & Applications, vol. 7, no. 1, pp. 1-11, 2018], aim to maximize efficiency across a wide band. Although these approaches are subject to limitations in meta-atom thickness and lens diameter, their overall efficiency remains notably high. Given that the paper's optimization framework concentrates solely on MTF, it would be valuable to address concerns regarding potential efficiency trade-offs. Particularly, could the efficiency suffer, and could this eventually pose issues for detectors, particularly when lens diameters are substantially reduced?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|65|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb65", "comment": "In Section 4.5, the authors mentioned that K is the PSF of the optical system from simulation. Can the authors further clarify how K was calculated analytically?", "reviewer_type": "human", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|65|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb65", "comment": "Could the authors explain why the Strehl ratio of the forward-designed hyperboloid metalens has a very low Strehl ratio of only 0.12 in Fig. 1b? And what is the angle of incidence when defining the Strehl ratio? Judging from data presented in Fig. S2, I expect a much higher Strehl ratio of the hyperboloid metalens (at the design wavelength) compared to the MTF-engineered ones.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|65|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb65", "comment": "Could the authors comment on whether efficiency is an issue in the case of broadband thermal imaging? Since polychromatic design will sacrifice efficiency a lot, especially when increasing the number of design wavelengths.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|65|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb65", "comment": "Throughout the design flow, angle of incidence is shown as a variable. Could the authors give information on how many angles are considered in calculating the PSFs?", "reviewer_type": "human", "label": "error", "error_type": "Neglect", "label_origin": "expert+llm-filter"}
{"id": "prb|65|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb65", "comment": "Could the authors comment on computational cost of the image deconvolution method? Does it support video framerate?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|65|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb65", "comment": "Typos: title for Fig.3, “Hyperboloid” instead of “Hyperbloid”. Figure captions for Fig. S2.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|67|Claude|1", "source": "prb", "split": "test", "paper_id": "prb67", "comment": "The paper's central claim of superior performance of multi-channel array (MCA) detectors compared to single-channel array (SCA) detectors is undermined by an unfair experimental comparison that uses different image resolutions and incompatible CNN architectures, invalidating the conclusions about MCA's advantage.\n\n\"to ensure fairness in subsequent image recognition, the total number of optoelectronic detectors simulated for infrared imaging is the same in both approaches. The difference lies in the fact that in the traditional single-channel array (SCA) photodetectors, one device corresponds to one pixel, while in the multi-channel array (MCA) photodetector, 6 devices form a single pixel... In other words, the MCA image has one-sixth the number of pixels compared to SCA.\" (Supplementary Section S5)\nThe authors claim fairness based on equalizing the total number of detectors, but this argument is flawed. In image classification tasks, image resolution is a critical factor that directly affects CNN performance. Reducing an image from 144×192 pixels (27,648 pixels) to 72×64 pixels (4,608 pixels) fundamentally changes the information content available for classification. The \"fairness\" claimed by equalizing detector count ignores the established relationship between image resolution and CNN performance demonstrated in multiple studies.\nFrom the supplementary section S6, for SCA: \"the input images size of 144×192 pixels... convolution layers of 5 × 5 × 20\" while for MCA: \"input images size of... 72×64 pixels, convolution layers of... 3 × 3 × 12\"\nThe CNN architectures are substantially different: SCA uses images of 144×192 with 5×5 convolutions and 20 filters, while MCA uses 72×64 images with 3×3 convolutions and 12 filters. Additionally, examining the code (CNN_Sensor_1.m lines 73-108), the SCA network uses maxPooling2dLayer(2,'Stride',2) while MCA uses maxPooling2dLayer(4,'Stride',4). These architectural differences make it impossible to attribute performance differences solely to the detector type, as the comparison confounds sensor type with CNN architecture and resolution.\n\"the MCA performs better than the SCA in gesture recognition accuracy. For example, at 10 epochs, the recognition accuracies of the MCA-based- and SCA-based detectors were 96.7% and 63.7%, respectively.\"\nThis dramatic accuracy difference is likely attributable to the different experimental conditions rather than inherent detector advantages. Research has shown that CNN performance varies significantly with input image resolution [[1]](#citation-list). The claim that MCA is superior for edge detection and gesture recognition cannot be validated when the comparison uses different image resolutions and network architectures, violating standard practices for fair model comparison [[2]](#citation-list).\n\nReferences:\n[1] Kandel, I., & Castelli, M. (2021). Impact of Image Resolution on Deep Learning Performance in Endoscopy Image Classification. Diagnostics, 11(12), 2183. https://pmc.ncbi.nlm.nih.gov/articles/PMC8700246/\n[2] Munien, C., & Viriri, S. (2022). Performance analysis of seven Convolutional Neural Networks (CNNs) with transfer learning for Invasive Ductal Carcinoma (IDC) grading in breast histopathological images. Scientific Reports, 12, 17900. https://www.nature.com/articles/s41598-022-21848-3", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|67|Claude|2", "source": "prb", "split": "test", "paper_id": "prb67", "comment": "The paper claims to demonstrate \"imaging capability of the fabricated array of infrared photodetectors,\" but the imaging experiments are conducted entirely through simulation using commercial camera data processed with mathematical filters, rather than actual measurements from the fabricated devices.\n\n\"To evaluate the imaging capability of the fabricated array of infrared photodetectors, we used the OPENZYNQ open-source project (https://github.com/openzynqhardware/openzynq.git) to simulate the process.\" (Main text, Methods section)\nThe word \"simulate\" directly contradicts the preceding phrase about evaluating \"the fabricated array.\" The authors did not actually use their photodetector array for imaging. Instead, they captured temperature data with a commercial Melexis infrared camera and applied mathematical transformations to simulate what their detectors might produce. This represents a fundamental disconnect between the device fabrication (which was real) and the imaging demonstration (which was simulated).\n\"For data collection, we employed a commercial Melexis infrared camera with 192×144 pixels to capture the desired temperature.\" (Supplementary Section S5)\nThe input data for the \"imaging demonstration\" comes from a commercial camera, not from the fabricated photodetector array. The MCA_Sensor.m code (lines 14-22) shows that Lorentzian filter functions are applied to this commercial camera data to simulate the spectral response of each channel. This is a mathematical simulation of expected detector behavior, not actual measurements from the fabricated devices.\n\n* Quote from code MCA_Sensor.m:\n```matlab\nfunction y = filter_Lorenz_1(x,B,delta_x)\n    y = B./(B+(x-delta_x).^2);\nend\n```\nThe code reveals that the \"multichannel imaging\" is achieved by applying Lorentzian mathematical filters to temperature data from a commercial camera. Each of the six channels (filter_Lorenz_1 through filter_Lorenz_6) applies a different filter function to simulate the spectral selectivity of the photodetector. This is fundamentally different from using actual photodetector array outputs for imaging, which would be required to validate claims about the \"imaging capability of the fabricated array.\"", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|67|Claude|3", "source": "prb", "split": "test", "paper_id": "prb67", "comment": "The paper reports specific accuracy values (98.1% and 98.2%) for gesture classification and edge detection without providing confidence intervals or standard deviations, despite the code showing that multiple Monte Carlo trials (M=100) were conducted, which undermines the reliability of the reported performance metrics.\n\n\"We also demonstrated enhanced and faster shape classification (98.1%) and edge detection (98.2%) using our multichannel infrared images compared with single-channel detectors.\" (Abstract)\nThese single-point accuracy values are reported without any indication of statistical uncertainty. Scientific best practices require reporting confidence intervals or standard deviations when making quantitative performance claims, particularly when the underlying experiments involve stochastic elements (random data splits, random weight initialization in CNNs, etc.). As noted in machine learning literature, \"confidence intervals around accuracy measurements can greatly enhance the communication of research results as well as impact the reviewing process\" [[3]](#citation-list).\n\n* Quote from CNN_Norm_1.m code (lines 38-42 and 51-53):\n```matlab\nM               = 100;\nEpochs_max      = 100;\n...\nResults = struct();\nResults.MatrixPr = zeros((Epochs_max-Epochs_min)/Epochs_delta + 1,M);\n```\nThe code clearly shows that M=100 Monte Carlo trials are performed, and results are stored in a matrix (Results.MatrixPr) with dimensions that accommodate all 100 trials. This data structure would enable calculation of means and standard deviations across trials. However, the paper only reports single accuracy values without the associated uncertainty measures that could be derived from these 100 trials. The code stores all trial results (line 97: Results.MatrixPr((Epochs-Epochs_min)/Epochs_delta + 1,m) = precision*100) but the paper does not report the distribution of these results.\n\"at 100 epochs, the recognition accuracy of the MCA approach reached a high level of 98.2%, whereas that of the SCA remained at ~69.7% (Fig. 4e).\"\nThe shaded regions visible in Figure 4c and 4e suggest some measure of variance was calculated, but the methodology for computing these bands is not described, nor are numerical values for standard deviations or confidence intervals provided in the text or supplementary materials. Proper statistical reporting would include explicit values such as \"98.2 ± X%\" where X represents the standard deviation or confidence interval derived from the 100 Monte Carlo trials.\n\nReferences:\n[3] Raschka, S. (2022). Creating Confidence Intervals for Machine Learning Classifiers. Sebastian Raschka Blog. https://sebastianraschka.com/blog/2022/confidence-intervals-for-ml.html", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|67|GPT|2", "source": "prb", "split": "test", "paper_id": "prb67", "comment": "The reported accuracy and speed advantages of MCA over SCA (e.g., 98.1% gesture classification and 98.2% curled-finger recognition) are not a robust comparison because the manuscript uses different effective image resolutions and different network architectures for SCA vs MCA and contains inconsistent reporting of training iterations per epoch, undermining the reliability of the conclusions drawn from Fig. 4.\n\n“In other words, the MCA image has one-sixth the number of pixels compared to SCA.”\nThis statement implies that the SCA and MCA learning tasks are performed on inputs with fundamentally different spatial sampling densities, so the comparison is not simply “single-channel vs multi-channel” at a fixed image resolution. A six-fold reduction in pixel count can change the difficulty of classification and edge recognition in nontrivial ways (e.g., altering aliasing, smoothing, and the amount of information presented per sample). Even if the authors aim to equalize the number of detectors, the resulting images are not matched in resolution, and thus the reported accuracy differences cannot be interpreted as an apples-to-apples improvement in an “imaging system.” This also directly complicates claims about “resolution enhancement,” since the MCA representation is explicitly lower-resolution spatially. The paper does not provide an ablation or normalization protocol (e.g., downsampling SCA to MCA resolution, or matching bandwidth and model capacity) to isolate the effect of multichannel spectral features. Without such controls, the causal attribution to the MCA hardware architecture is not sufficiently supported.\n“However, we analyzed the changes in classification accuracy over 100 epochs for gesture recognition, with each epoch consisting of 3,600 iterations.”\nThis sentence defines a concrete training schedule (3,600 iterations per epoch) that is subsequently used to argue about faster training and higher accuracy. Training speed comparisons are sensitive to the definition of an “iteration” and to how many gradient updates are performed. If iteration counts are misreported or inconsistent across conditions, the claimed speedup could be an artifact of mismatched training budgets rather than a property of the imaging representation. The manuscript does not clarify whether “iterations” correspond to mini-batches, full passes through the data, or another unit, which is necessary for reproducing Fig. 4b–e. This ambiguity weakens the interpretability of the reported learning curves and the claim that MCA is “significantly faster.”\n“(b, c) Evolution of classification accuracy over 100 epochs for gesture recognition, with each epoch consisting of 1,000 iterations. (d, e) Changes in the classification accuracy over 100 epochs for curled finger recognition, with each epoch including 1,000 iterations.”\nThe figure caption directly contradicts the main-text statement that an epoch consists of 3,600 iterations, instead stating 1,000 iterations per epoch. This discrepancy is substantial (a 3.6× difference in update counts) and undermines claims about both speed and convergence behavior, because learning curves would shift significantly under these different training budgets. It also makes it unclear how the reported headline numbers (e.g., 98.1%, 98.2%) were obtained and under what computational cost. Such internal inconsistencies are particularly problematic when the paper’s motivation includes “faster training and recognition speeds.” A reader cannot reproduce or fairly interpret the learning results without a single, consistent definition. The inconsistency therefore materially affects the reliability of the manuscript’s conclusions.\n```matlab\nX = reshape(images, [144,192,1,length(images)]);\nX_2 = reshape(images_new, [72,64,1,length(images_new)]);\n...\nlayers = [...\n          imageInputLayer([144,192,1]);\n          ...\n          convolution2dLayer(5,20);\n          ...\n          fullyConnectedLayer(NumberOfFeature);\n          ...\n        ];\n...\nlayers = [...\n          imageInputLayer([72,64,1]);\n          ...\n          convolution2dLayer(6,12);\n          ...\n          fullyConnectedLayer(NumberOfFeature);\n          ...\n        ];\n```\nThis code shows that the MCA and SCA models differ simultaneously in input resolution (144×192 vs 72×64) and in network architecture/hyperparameters (e.g., convolution kernel sizes and channel counts, pooling stride). That means the reported performance gap cannot be attributed solely to the sensor modality (single-channel vs multi-channel), because the classifier capacity and inductive biases are also changed. In standard comparative evaluations, one would either hold the model fixed and change only the representation, or perform capacity-matched models with careful justification. Here, the code implements different architectures and pre-processing paths, creating a confounded comparison. Additionally, the manuscript text does not disclose these architectural differences in enough detail to reconstruct them without the code. As a result, the reported accuracy and “faster” learning behavior are not convincingly tied to the proposed detector concept.\n“However, by partitioning the available data into three sets, we drastically reduce the number of samples which can be used for learning the model, and the results can depend on a particular random choice for the pair of (train, validation) sets.” ([5](https://scikit-learn.org/stable/modules/cross_validation.html))\nThis guidance highlights that train/validation/test splitting introduces variance that depends on the random partition, especially when datasets are limited or heterogeneous. The manuscript does not specify the data splitting protocol for Fig. 4 (e.g., fixed split, cross-validation, stratification, subject-wise split), yet it draws strong conclusions from single reported accuracy curves. Given the paper’s emphasis on small-sample behavior (“when dealing with a small sample size”), sensitivity to split choice becomes particularly important. Without reporting how splits were chosen and without providing variability estimates across splits/seeds, the observed MCA–SCA gaps could reflect a favorable partition rather than a robust property of the multichannel imaging representation. This is a widely recognized issue in ML evaluation, and the paper does not address it. Therefore, the comparison as presented is not methodologically solid.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|67|GPT|3", "source": "prb", "split": "test", "paper_id": "prb67", "comment": "The manuscript does not provide sufficient access to the underlying data and runnable artifacts needed to reproduce the key imaging and learning results, and the provided code bundle contains Git LFS pointer files instead of the actual .mat datasets, which prevents independent verification and materially weakens the paper’s methodological transparency.\n\n“Data supporting the findings of this study are available from the corresponding authors upon request.”\nThis policy prevents immediate independent reproduction of the key claims (spectral response curves, responsivity comparisons, and especially the learning results in Fig. 4). In contemporary experimental nanophotonics/optoelectronics and machine-learning-for-imaging work, it is common practice to release at least the processed datasets and scripts required to regenerate the main figures, even if some raw data are large. “Upon request” introduces friction, delays, and selective availability, and it impedes routine verification by reviewers and readers. This is particularly problematic here because the headline claims rely on quantitative learning metrics (98.1%, 98.2%) and on a simulation pipeline whose assumptions need to be inspected. Without public access, it is not possible to audit preprocessing, label generation, or potential leakage between training and test sets. As a result, the reported conclusions cannot be independently validated.\n“/***************************************************/\nPlease use git lfs to clone this project.\n/***************************************************/”\nThis instruction indicates that key artifacts are stored via Git Large File Storage rather than directly in the repository. For a reproducibility package to be usable, readers must be able to obtain the actual large objects, not only the pointer files. In practice, many archival contexts (including paper supplementary bundles) do not automatically fetch Git LFS objects, leaving users with incomplete datasets. The paper does not provide a stable, explicit data archive (e.g., Zenodo/OSF) that guarantees long-term access to the LFS-managed objects. This creates a high risk that the code package will not run for most readers, undermining reproducibility. The issue is not merely documentation quality; it directly blocks re-running the reported experiments.\n```text\nversion https://git-lfs.github.com/spec/v1\noid sha256:cc43087b78145cddd9706b2ee37ffc9d04b752a9960f5a82c5fbaa73d42b9e0c\nsize 95533190\n```\nThis file content shows that the supposed dataset file is a Git LFS pointer, not an actual MATLAB .mat data file containing images/labels. Consequently, running the provided CNN scripts as-is will fail because the expected variables (e.g., image tensors and labels) are not present. This directly prevents reproduction of the reported learning curves and accuracy numbers, which are central to the paper’s conclusions about multichannel meta-imaging. A reader cannot even inspect the dataset statistics (class balance, number of samples, train/test splits) because the real data are missing. This is a severe reproducibility failure for a results-driven paper. It also impedes checking whether the simulation pipeline matches the manuscript’s descriptions.\n“The core Git LFS idea is that instead of writing large blobs to a Git repository, only a pointer file is written.” ([1](https://raw.githubusercontent.com/git-lfs/git-lfs/main/docs/spec.md))\nThis specification statement explains why the repository can contain small text files in place of actual binary datasets. In the provided code bundle, multiple .mat files are exactly such pointers, meaning the repository does not actually include the data required to execute the experiments. Unless the corresponding LFS objects are fetched from the original remote, a third party cannot reproduce the work using the supplied materials. For archival reproducibility, it is important that the full artifacts be obtainable from stable links independent of a particular Git hosting configuration. The manuscript does not provide such an archive, and its “upon request” data policy compounds the problem. Therefore, the reproducibility gap is structural rather than incidental.\n“Reproducibility, that is obtaining similar results as presented\nin a paper or talk, using the same code and data (when available), is a necessary step to\nverify the reliability of research findings.” ([2](https://jmlr.org/papers/volume22/20-303/20-303.pdf))\nThis definition underscores that the combination of code and data access is necessary for verifying the reliability of quantitative claims. The paper’s main learning-based conclusions (gesture recognition and curled-finger edge detection) are exactly the kind of results where subtle data-processing choices can alter outcomes. Providing code without the actual datasets (or with datasets gated by request) does not satisfy the basic reproducibility standard described here. Moreover, the manuscript makes strong performance and speed claims that require re-running training to confirm. The current artifact state prevents that, weakening confidence in the reported improvements. This is a major methodological shortcoming given modern expectations for reproducible computational experiments.\n“A1. (meta)data are retrievable by their identifier using a standardized communications protocol” ([3](https://www.nature.com/articles/sdata201618))\nThis FAIR principle articulates a widely adopted baseline expectation that data should be retrievable in a standardized way, not only through private correspondence. While not every project can immediately release all raw data, the paper’s central quantitative claims depend on datasets and simulation outputs that should be made programmatically accessible for verification. The provided materials do not include resolvable identifiers (e.g., DOIs) for the datasets underlying Fig. 4’s learning curves, and the Git LFS pointers demonstrate that the included “data files” are not directly retrievable in the shared package. This hinders reuse and independent audit of the work. Aligning with FAIR typically entails depositing data in a stable repository with clear identifiers and access protocols. The manuscript does not meet this standard for the computational parts of its contribution.", "reviewer_type": "ai", "label": "error", "error_type": "Neglect", "label_origin": "expert+llm-filter"}
{"id": "prb|67|GPT|4", "source": "prb", "split": "test", "paper_id": "prb67", "comment": "The manuscript reports key quantitative metrics (photoresponsivity and learning accuracies) largely as single-point values without uncertainty estimates, despite averaging procedures and clear sources of variability (device-to-device variation, wavelength-dependent noise, and training randomness), which weakens the reliability of the quantitative conclusions.\n\n“All the photocurrents were obtained by averaging the peak values from 12 points under illumination at different wavelengths. … For the photodetector demonstrated herein, it achieved an enhanced photoresponsivity of approximately 30 mA W\\(^{-1}\\).”\nThe manuscript explicitly averages photocurrent peaks across 12 measurements, which implies there is an underlying distribution of values and therefore a measurable uncertainty (e.g., standard deviation or standard error). However, the paper does not report dispersion measures, confidence intervals, or device-to-device variability associated with the quoted responsivity value. In photodetector characterization, responsivity and spectral selectivity are often sensitive to alignment, local heating, contact resistance, and sample inhomogeneity; averaging without reporting spread obscures these effects. Without uncertainty, it is difficult to assess whether the stated “approximately 30 mA W\\(^{-1}\\)” is statistically distinguishable from prior art comparisons or from cell-to-cell variation within the array. This affects the strength of the claims about “selective responsivity” and comparability to other devices. The lack of uncertainty reporting therefore weakens the quantitative support for the device-performance narrative.\n“For example, at 100 epochs, the recognition accuracies of the MCA and SCA were 98.1% and 93.2%, respectively.”\nThe paper presents learning performance as single accuracy values, but it does not report how many independent runs were performed, whether random seeds were controlled, or what the variability across runs/splits is. This omission matters because the claimed improvements (e.g., +4.9 percentage points for gesture recognition at 100 epochs) could change under different random initializations or dataset partitions. The manuscript also emphasizes “small sample size” regimes where performance variance is typically higher, making uncertainty quantification even more important. Without standard deviations or confidence intervals, it is unclear whether the performance gaps are robust or within run-to-run variability. In addition, the paper’s speed claims depend on training dynamics, which are also stochastic and should be summarized across repeats. As written, the results are not statistically grounded.\n```matlab\nM               = 100;\n...\nfor Epochs=Epochs_min:Epochs_delta:Epochs_max\n    for m=1:M\n        idx = randperm(length(images));\n        ...\n        [net_cnn,info] = trainNetwork(X_train,Y_train,layers,options);\n        testLabel = classify(net_cnn,X_test);\n        precision = sum(testLabel==Y_test)/numel(testLabel);\n        Results.MatrixPr(...,m) = precision*100;\n    end\nend\n```\nThis code explicitly performs 100 randomized trials (M = 100) with random permutations of the data and records a distribution of test-set precision values. That implies the authors are aware that performance varies across random splits/runs and that summary statistics across trials are meaningful. Yet the manuscript reports single accuracy numbers (e.g., 98.1%, 98.2%, 69.7%) without disclosing the distribution, mean±error, or even whether those numbers are averages, medians, or best-case runs. Omitting this information prevents readers from assessing statistical significance and robustness of the claimed improvements. It also creates ambiguity about whether results could be reproduced under the same procedure. Given that the code is structured to collect variability, the paper should report it; otherwise, the quantitative claims are not adequately supported.\n“All results (including graphs) show mean and standard error across random seeds.” ([4](https://arxiv.org/pdf/1709.06560.pdf))\nThis statement exemplifies a common and recommended reporting practice in learning-based studies: summarize results over multiple random seeds with uncertainty (standard error) rather than a single curve/value. The manuscript under review makes strong claims about accuracy and speed advantages, but it does not report analogous uncertainty measures, even though its own code suggests randomized repetitions. Without such reporting, it is difficult to compare methods fairly or to determine whether improvements are robust. The absence of variability estimates is especially problematic given the paper’s emphasis on small-sample learning and on differences in convergence speed. Adopting mean±error reporting would materially strengthen the evidentiary basis for the conclusions. As it stands, the statistical treatment is incomplete.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|67|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb67", "comment": "The paper's central claim of demonstrating \"multichannel meta-infrared imaging\" is based on a scientifically invalid simulation that treats pixel intensity as a proxy for spectral wavelength.\n\n```matlab\nfunction Im_Sensor = MCA_Sensor(Im_Origin)\n    ...\n    for i=1:72\n        for j=1:64\n            Im_1(i,j) = Im((i-1)*2+1,(j-1)*3+1)*filter_Lorenz_1(Im((i-1)*2+1,(j-1)*3+1),B,delta_x);\n            ...\n```\nThis code snippet from `MCA_Sensor.m` reveals that the authors simulate the \"spectral response\" of their detector by applying a Lorentzian filter (`filter_Lorenz_1`) directly to the pixel intensity values (`Im(...)`) of a broadband infrared image. In physics, a spectral response function $R(\\lambda)$ describes how a detector responds to different wavelengths of light. The signal is the integral of the incident spectrum weighted by this response: $S = \\int I(\\lambda) R(\\lambda) d\\lambda$. However, the authors' code implements $S = I_{pixel} \\times L(I_{pixel})$, where $L$ is a Lorentzian function of the *integrated intensity* $I_{pixel}$. This implies that the \"resonant wavelength\" of the detector depends on how bright the pixel is, which is physically nonsensical. A brighter object does not change the wavelength of light it emits in a way that matches this function, nor does a detector's spectral response depend on the incident intensity (in the linear regime). This methodology essentially applies a non-linear intensity transformation (tone mapping) to the image and falsely presents it as \"multichannel spectral imaging.\"\n```matlab\nfunction y = filter_Lorenz_1(x,B,delta_x)\n    y = B./(B+(x-delta_x).^2);\nend\n```\nThe `filter_Lorenz_1` function takes the pixel value `x` (a scalar representing brightness) and uses it as the independent variable in a Lorentzian distribution. This confirms that the simulation treats intensity as the spectral variable. Consequently, the \"multichannel\" images generated are merely intensity-sliced versions of the original broadband image (e.g., Channel 1 highlights dark pixels, Channel 6 highlights bright pixels), containing no actual spectral information. The reported \"enhanced\" imaging capabilities are therefore artifacts of this artificial image processing, not a result of the proposed device's physics.\n\"IRISIM is an imaging and video simulation program that models and simulates the entire imaging process of broadband and multispectral infrared imaging systems.\" [1]\nEstablished simulation tools for multispectral imaging, such as IRISIM, require modeling the spectral radiance of the scene and the spectral response of the sensor separately. The authors' approach of generating \"multispectral\" data from a single broadband image without any spectral information about the scene is methodologically unsound and contradicts standard practices in the field.\n\nReferences:\n[1] G. Gerhart, T. Meitzler, E. Sohn, and H. Choe, \"IRISIM: infrared imaging simulator,\" in *Targets and Backgrounds XI: Characterization and Representation*, vol. 5784, pp. 190-200, International Society for Optics and Photonics, 2005. https://doi.org/10.1117/12.606524", "reviewer_type": "ai", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|67|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb67", "comment": "The comparison between the proposed Multichannel Array (MCA) and the Single-Channel Array (SCA) is misleading because the MCA data is derived from the SCA data via the flawed simulation described above, effectively comparing a raw image to a processed, edge-enhanced version of itself.\n\n\"It is worth noting that... in the traditional single-channel array (SCA) photodetectors, one device corresponds to one pixel, while in the multi-channel array (MCA) photodetector, 6 devices form a single pixel... In other words, the MCA image has one-sixth the number of pixels compared to SCA.\"\nThe authors state that the MCA image has significantly lower resolution (1/6th) than the SCA image. In a fair comparison, lower resolution typically leads to worse performance. However, the authors claim superior performance for MCA. This counter-intuitive result is explained by the fact that the \"MCA\" images are generated by summing the intensity-filtered channels (as seen in `MCA_Sensor.m`: `Im_Sensor = Im_1+ Im_2+...`), which acts as a non-linear contrast enhancement or edge detection filter. The comparison is thus not between two hardware technologies, but between a raw broadband image and a digitally processed version of the same image where edges have been artificially highlighted by the intensity-slicing simulation.\n\"The target temperature were captured using a commercial camera (Melexis, 192×144 pixels).\"\nThe input data for both SCA and MCA simulations comes from a commercial Melexis camera, which is a broadband thermal imager [2]. Since the source data contains no spectral resolution (it integrates radiation over a wide band, typically 8-14 $\\mu$m), it is impossible to extract 6 distinct spectral channels from it without hallucinating information. The \"spectral\" differences claimed between MCA channels are purely mathematical artifacts of the intensity-based filtering described in Item 1. Therefore, the claim that MCA provides \"enhanced recognition accuracy\" due to \"multichannel meta-infrared imaging\" is unsupported by the data.\n\nReferences:\n[2] Melexis, \"MLX90640 32x24 IR array datasheet,\" Melexis NV, 2019. https://www.melexis.com/en/product/mlx90640/far-infrared-thermal-sensor-array", "reviewer_type": "ai", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|67|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb67", "comment": "The authors frame the standard technique of ferroelectric domain writing using scanning probe microscopy as a novel \"type-printing\" method, which exaggerates the originality of their fabrication approach.\n\n\"As early as the Qingli period of the Song Dynasty... China's Bi Sheng... invented the clay type... marking the birth of the movable-type printing technique... Figure 2a illustrates the fabrication process... designed using the type-printing technique employed in this study\"\nThe authors draw a parallel between their method and the invention of movable type printing. However, the technique they use—writing ferroelectric domains with a conductive AFM tip—is a well-established method known as \"ferroelectric lithography\" or \"domain patterning,\" which has been used for decades [3]. Framing this serial, scanning-probe-based process as \"type-printing\" is misleading, as it lacks the parallel processing capability inherent to printing. The \"engraving\" and \"printing\" analogy adds unnecessary jargon without contributing to the technical understanding or novelty of the method.\n\"Ferroelectric Lithography of Multicomponent Nanostructures\" [3]\nThis seminal paper from 2004 (and many others since) describes the exact process of using AFM tips to pattern ferroelectric domains and subsequently assemble materials (like metals or particles) on the surface. The authors' method of transferring graphene onto pre-patterned domains is an application of this known technique, not a fundamentally new \"printing\" invention as the terminology suggests.\n\nReferences:\n[3] S. V. Kalinin, D. A. Bonnell, T. Alvarez, X. Lei, Z. Hu, J. H. Ferris, Q. Zhang, and S. Dunn, \"Ferroelectric lithography of multicomponent nanostructures,\" *Advanced Materials*, vol. 16, no. 9-10, pp. 795-799, 2004. https://doi.org/10.1002/adma.200305702", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|67|Gemini|5", "source": "prb", "split": "test", "paper_id": "prb67", "comment": "The paper attributes the zero-bias operation to the ferroelectric superdomain and plasmonic resonance, but the device structure employs asymmetric metal contacts, which are the likely cause of the photovoltaic effect.\n\n\"In this study, we employed an asymmetric metal-doping scheme... Specifically, we deposited 20-nm-thick layers of palladium (Pd) and titanium (Ti) onto a graphene sheet\"\nThe use of asymmetric contacts (Pd and Ti) creates a built-in electric field across the graphene channel due to the work function difference between the metals. This is a standard method to achieve zero-bias photocurrent in graphene photodetectors [4]. The paper claims that the \"ferroelectric superdomain... confining graphene plasmons\" is responsible for the performance, but does not adequately decouple the contribution of the asymmetric contacts from the ferroelectric doping. It is highly probable that the zero-bias current is primarily driven by the contact asymmetry, while the superdomain merely modulates the absorption. The explanation of the device physics is therefore incomplete and potentially misleading regarding the role of the \"meta-imaging\" structure.\n\"Another interesting phenomenon is that the device we designed can operate at zero bias voltage... This coincided with the biological thermal radiation\"\nOperating at zero bias is a direct consequence of the asymmetric contact design, not a \"phenomenon\" related to the biological thermal radiation or the superdomain structure itself. The causal link between the device architecture and its operating mode is not clearly established, and the paper conflates the spectral selectivity (due to plasmons) with the charge collection mechanism (due to contacts).\n\nReferences:\n[4] T. Mueller, F. Xia, and P. Avouris, \"Graphene photodetectors for high-speed optical communications,\" *Nature Photonics*, vol. 4, no. 5, pp. 297-301, 2010. https://doi.org/10.1038/nphoton.2010.40", "reviewer_type": "ai", "label": "error", "error_type": "Neglect", "label_origin": "expert+llm-filter"}
{"id": "prb|67|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb67", "comment": "The characterization of photodetectors appears incomplete, as the authors solely focus on responsivity, where they claim the device performance is already comparable to conventional graphene devices. However, the absence of essential characterizations such as detectivity and frequency dependence from their measurements detracts from the overall quality of the presentation. This is particularly concerning considering that they only present the transmission and photoresponse of a single device array in this manuscript.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|67|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb67", "comment": "In the manuscript, the authors argue that \"current graphene plasmonic photodetectors employing top- or back-gate layers face common limitations in terms of complex fabrication of contact electrodes and high power consumption.\" This implies that the type-printing technique simplifies the fabrication complexity. However, controlling the ferroelectric domain is achieved through conductive AFM, which, based on my experience, is very time-consuming. I disagree with the argument that the type-printing technique can alleviate fabrication issues in plasmonics.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|67|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb67", "comment": "How did the authors determine that the infrared sensitivity characteristics derive from the graphene plasmon resonance effect rather than ferroelectric thin films? Since the ferroelectric materials usually had thermoelectric effect, how could the author separate the contribution from graphene and the BFO?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|67|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb67", "comment": "The device arrays exhibit a tunable spectral response within 1084~1292 cm-1 by rescaling the ferroelectric super-domain width. Can it be extended to a wider infrared frequency range? The authors had published a simulation paper before (Nanoscale, 2019,11, 20868-20875), and the responsibility could be achieved much higher than the measured results. What’s the reason and how to improve the responsivity in future devices?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|67|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb67", "comment": "Why is it that the single-channel imaging recognition result is always approximately 60%?", "reviewer_type": "human", "label": "error", "error_type": "Inaccurate Summary", "label_origin": "expert+llm-filter"}
{"id": "prb|67|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb67", "comment": "Why did the authors choose a range of 100~500 nm instead of others for BFO polarization width? Can the author extend the wavelength range to 3-5 μm range?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|67|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb67", "comment": "Some non-technical issues should also be addressed. For example, in Fig. 3d, I think that the author's intention is to emphasize the highest responsivity of the device array, but the current version is not clear enough. The scale bars in Fig. 2b,c are missing.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|67|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb67", "comment": "The authors brand their devices as using the “type-printing” technique, but is it what people usually call it? Or is it the authors’ invention? I can kind of relate to the comparison to the movable-type printing that the authors mention at the beginning of the “Type-printing of photodetector” section. But I am afraid this comparison is a little bit of a stretch.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|67|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb67", "comment": "The authors mention that a downward domain dopes the graphene heavily, but an upward domain does not. Why does the doping of graphene depend on the polarization of the underneath substrate? The authors should explain and give references.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|67|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb67", "comment": "Looks to me the authors measured the infrared transmission in an uncommon fashion. They used an AFM probe to direct light? And how did they perform the measurements? The authors need to fully explain their measurement scheme (namely, Figure 3c).", "reviewer_type": "human", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|67|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb67", "comment": "How the authors measured the photocurrent is also unclear to me. The readers would need more information on methods to understand and reproduce the results in the manuscript. Drawing some schematics and adding some paragraphs would help.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|67|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb67", "comment": "Figure 3a. I assume the scale bar of 1 \\( \\mu \\)m is for the PFM images, not for the optical image? If so, what is the scale of the optical image?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Claude|1", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "The paper includes a non-significant PLS dimension (p = 0.103) among the \"four functional dimensions\" used to support the main convergence claims, which weakens the statistical foundation of the conclusions.\n\n\"The first four dimensions (or pairs of latent variables) together accounted for 93.8% of the summed squared covariances between the two blocks of variables (hierarchical permutation tests against a null hypothesis of no association yielded p-values of 0.001, 0.030, 0.043, and 0.103, respectively, for the four dimensions).\"\nThe fourth PLS dimension has a p-value of 0.103, which exceeds the conventional significance threshold of 0.05 and even the more lenient threshold of 0.10 sometimes used in exploratory analyses. Despite this, the authors include it as one of the \"four functional dimensions\" that form the basis of their convergence analysis. This is problematic because the permutation test was specifically designed to determine whether each dimension captures a meaningful association between labyrinth shape and contextual variables. A p-value above 0.10 indicates that the observed covariance for PLS4 could reasonably have arisen by chance, undermining its interpretation as a true functional signal.\n\"Given the importance of habitat and locomotor behaviour to a species' morphological adaptations, the four PLS dimensions described above estimate the 'functional' aspects of labyrinth shape and - by and large - separate the functional part of shape space from those shape features that carry no or little functional signal.\"\nThis statement presents all four dimensions as equally valid estimators of \"functional aspects\" of labyrinth shape, despite one dimension failing to achieve statistical significance. Standard practice in morphometric PLS analysis would be to either exclude non-significant dimensions from functional interpretation or clearly acknowledge the marginal status of PLS4. The claim that these four dimensions \"separate the functional part of shape space\" from non-functional features rests on all four dimensions being statistically supported, which is not the case here.\n\"When computed only from these four PLS dimensions, the average shape distance for pairs of non-analogues was even 42.0% higher than for pairs of analogues (p<0.001), reflecting strong convergent evolution of these shape features.\"\nThe dramatic increase from 18% (full data) to 42% (four PLS dimensions) difference between analogues and non-analogues is partially attributable to including the non-significant PLS4. Including a dimension that may represent noise rather than functional signal inflates the apparent strength of convergence. A more conservative analysis using only the three significant dimensions (p < 0.05) would provide a more robust estimate of convergent evolution.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Claude|2", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "The study tests whether afrotherians resemble their non-afrotherian analogues more closely than non-analogues, but the analogues were defined a priori based on expected morphological and ecological similarities, which introduces potential confirmation bias into the convergence analysis.\n\n\"To this end, we compare bony labyrinth shape of 20 afrotherian taxa to that of 20 other, morphologically and ecologically analogous mammals using 3D geometric morphometrics and a multivariate phylogenetic comparative approach.\"\nThe analogues were selected before the analysis based on presumed similarities in morphology and ecology. This creates a circularity: species are designated as analogues because they occupy similar ecological niches and have similar body plans, and then the analysis tests whether these same species also have similar inner ear shapes. Unlike phylogenetically rigorous convergence tests that assess whether lineages have independently evolved toward similar phenotypes from dissimilar ancestors, this approach assumes convergence in the study design itself.\n* Quote from [Stayton 2015](https://onlinelibrary.wiley.com/doi/abs/10.1111/evo.12729): \"convergence occurs when two taxa evolve to be more similar to one another than their ancestors were to each other\"\nThis definition from the convergence literature emphasizes that true convergence requires demonstrating that lineages have become more similar over evolutionary time. The authors' approach of comparing pre-selected analogues to non-analogues tests for current phenotypic similarity among ecologically similar species, but does not directly test whether this similarity arose through convergent evolutionary trajectories from more dissimilar ancestral states. The C-measures developed by [Stayton (2015)](https://onlinelibrary.wiley.com/doi/abs/10.1111/evo.12729) or theta-based methods that reconstruct ancestral states would provide more rigorous tests of convergent evolution that are independent of a priori groupings.\n* Quote from [Quantification provides a conceptual basis for convergent evolution (Speed & Arbuckle 2017)](https://pmc.ncbi.nlm.nih.gov/articles/PMC6849873/): \"Alternative distance-based methods for testing for convergence such as Wheatsheaf index (Arbuckle et al., 2014; Arbuckle and Minter, 2015) and θ (Castiglione et al., 2019) cannot adequately differentiate between convergence and either conservatism or geometric parallelism because phenotypic distances between ancestral morphologies are not considered\"\nWhile the authors do calculate the Wheatsheaf index in their code (W = 1.183), this metric—like their primary Procrustes distance approach—relies on a priori designation of focal species and cannot distinguish true convergence from ancestral similarity (phylogenetic conservatism) or geometric parallelism. The paper would benefit from ancestral state reconstruction to demonstrate that the labyrinth shapes of analogue pairs diverged from more dissimilar ancestors, rather than simply maintaining ancestral similarities.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Claude|3", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "The paper's main conclusion about the \"high evolvability\" of the mammalian inner ear is presented as supported by the convergence data, but evolvability is a distinct concept from convergence that requires evidence about heritable variation and developmental capacity, which was not measured.\n\n\"We suggest that this evolvability is a direct consequence of the increased genetic and developmental complexity of the mammalian ear compared to other vertebrates.\"\nThis is presented as a suggestion rather than a tested hypothesis. Evolvability is formally defined as the capacity to generate heritable phenotypic variation in response to selection, which depends on the genetic variance-covariance (G) matrix structure, heritability, and developmental modularity. The observed convergence patterns are consistent with high evolvability but do not directly measure it. Convergence could also arise from strong directional selection on a structure with moderate evolvability, or from conserved developmental constraints that channel variation along similar phenotypic trajectories.\n* Quote from [Le Maître et al. 2020](https://pmc.ncbi.nlm.nih.gov/articles/PMC7399675/): \"We propose a novel hypothesis: The incorporation of the bones of the primary jaw joint into the middle ear has considerably increased the genetic, regulatory, and developmental complexity of the mammalian ear. This increase in the number of genetic and developmental factors may, in turn, have increased the evolutionary degrees of freedom for independent adaptations\"\nThe evolvability hypothesis is explicitly framed as a proposal in the authors' prior work, requiring empirical testing. The current study provides correlational evidence (convergent phenotypes in convergent environments) but does not test the mechanistic claim about genetic and developmental complexity enabling independent adaptation. Testing this hypothesis would require comparative developmental genetics, quantitative genetic studies of ear variation within species, or comparative analyses that quantify the dimensions of ear shape variation relative to other vertebrate groups.\n\"While convergent evolution in traits such as body size, body proportions, and life history traits is well documented and easy to understand, it is less obvious how the vertebrate ear realises such a stunning evolvability.\"\nThe paper acknowledges that evolvability of the ear is \"not obvious\" given its spatial constraints and early developmental completion. However, the study design cannot distinguish between multiple explanations for the observed convergence: (1) high evolvability enabling adaptive responses, (2) strong selection overcoming developmental constraints, or (3) constrained developmental variation that channels phenotypic responses to similar environmental pressures along similar trajectories. Without comparative data on developmental or genetic variation, the evolvability claim remains speculative.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Claude|4", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "The study uses a single specimen per species without quantifying or correcting for within-species variation or measurement error, which may affect the reliability of species mean estimates used in phylogenetic comparative analyses.\n\n\"We landmarked a single bony labyrinth per species. As we are dealing with a sample of disparate taxa, most of which are separated by long evolutionary time spans, interspecific variation likely far exceeds within-species variation.\"\nWhile the assumption that interspecific variation exceeds intraspecific variation is reasonable for broadly sampled taxa, the magnitude of this ratio affects the reliability of comparative analyses. Recent methodological work has shown that ignoring intraspecific variability can increase Type I error rates in phylogenetic comparative methods, particularly when sample sizes are small and intraspecific variances are substantial. A single specimen cannot capture the mean phenotype reliably if within-species variation is non-negligible relative to among-species differences.\n* Quote from [Garamszegi & Møller 2010](http://www.italian-journal-of-mammalogy.it/pdf-77240-13393?filename=13393.pdf) as cited in morphometric literature: \"it has been shown that ignoring intraspecific variability can lead to increased type I error rates when intraspecific variances are large and sample sizes are small\"\nThe authors acknowledge in the Methods that they \"did not consider within-species variation, sexual dimorphism, and bilateral asymmetry\" because they \"aimed to maximise taxonomic, phylogenetic, and ecological breadth of the sample.\" While this trade-off is understandable given practical constraints, it means the precision of species-level shape estimates is unknown. Modern phylogenetic comparative methods can incorporate measurement error and within-species variation, which would strengthen the analysis by properly weighting species estimates by their reliability.\n\"Bony labyrinth morphology is only slightly sexually dimorphic (Braga et al., 2019; Boucherie et al., 2021), likely rendering dimorphism negligible compared to the disparity across species\"\nThe authors cite studies on sexual dimorphism but do not provide quantitative estimates of within-species variation for the labyrinth traits in their sample. For closely related species pairs (e.g., within elephant shrews or golden moles), within-species variation could represent a non-trivial fraction of between-species differences. The permutation tests used for inference assume that species values are measured without error, which may inflate significance when measurement uncertainty is ignored.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|GPT|1", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "This paper overstates its main conclusion by claiming it demonstrates high evolvability of the mammalian inner ear, even though the analyses only establish phenotypic convergence and ecology–shape covariation and do not quantify evolvability in the quantitative-genetic sense; this undermines both Validity and Conclusions for the title/abstract-level claim.\n\n\"Using a new multivariate approach, we show that in Afrotheria, a monophyletic clade with morphologically and ecologically highly disparate species, inner ear shape evolved similar adaptations as in non-aфrotherian mammals. We identified four trait combinations that underlie this convergence. The high evolvability of the mammalian ear is surprising: nowhere else in the skeleton are different functional units so close together; it includes the smallest bones of the skeleton, and is encapsulated within the densest bone. We suggest that this evolvability is a direct consequence of the increased genetic and developmental complexity of the mammalian ear compared to other vertebrates.\" \nThis passage explicitly equates the paper’s empirical result (a pattern of convergence and covariation) with a strong mechanistic claim about “high evolvability” and its genetic/developmental cause. However, the paper does not estimate additive genetic variance/covariance, mutational variance, or any other standard quantity used to operationalize evolvability, nor does it test alternative developmental-genetic explanations. The leap from macroevolutionary convergence to intrinsic evolvability is not logically necessary: convergence can occur under strong selection even when evolvability is modest, and conversely high evolvability does not guarantee repeated convergence. Because this claim appears in the abstract and title framing, it substantially shapes how readers interpret the results. Without a direct measurement or a clear inferential bridge, the stated conclusion is not supported at the evidentiary level presented here.\n\"Our results thus indicate that functional adaptation and convergence dominate over phylogenetic history in the pattern of similarity in inner ear shape at the level of major placental mammal clades, supporting the hypothesis that the mammalian ear has high evolvability.\" \nThis sentence ties the distance-based convergence result to a hypothesis about evolvability, but it does not specify what observable implication of evolvability is being tested beyond “convergence exists.” In quantitative genetics and macroevolution, evolvability is typically assessed relative to a defined selection direction or via the structure of (genetic) variance; by contrast, this paper uses ecological similarity as an organizing principle and then interprets convergence as evidence of evolvability. The conclusion also implicitly assumes that convergent outcomes reflect internal “degrees of freedom” rather than shared constraints or repeated selection on a limited set of feasible morphologies. Because the paper does not measure genetic/developmental variation or compare the inner ear’s response capacity to other anatomical systems, the inference remains speculative. As written, the claim risks being read as a demonstrated property rather than a hypothesis.\n\"Although the current study did not comprise a comparison with non-mammals, our findings nonetheless offer support for this evolvability hypothesis.\" \nHere the authors acknowledge a missing comparative baseline (non-mammals) while still asserting evidentiary support for an evolvability hypothesis that is explicitly framed as mammal-versus-other-vertebrates in the abstract. If the proposed cause is “increased genetic and developmental complexity … compared to other vertebrates,” then some cross-vertebrate comparison or direct developmental-genetic evidence would be expected to support the causal direction. In its absence, the paper can at most argue that mammalian inner ears show convergent ecological patterning within the sampled mammals. This matters because the paper’s title/abstract generalize beyond the scope of the data analyzed. Stating the limitation does not repair the mismatch between claim strength and what is actually tested.\n\"The first is to compare evolvabilities, or ability to respond to selection\" ([1](https://pmc.ncbi.nlm.nih.gov/articles/PMC1204793/)).\nThis definition clarifies that evolvability is fundamentally about a population’s capacity to respond to selection, typically grounded in genetic (co)variation and selection gradients. The present paper does not estimate such quantities and instead bases its argument on phenotypic convergence and multivariate covariation with ecological proxies. Without connecting observed phenotypic patterns to underlying heritable variation or response-to-selection metrics, the paper cannot claim to have demonstrated evolvability in the sense used in the evolvability literature. This gap is not a minor semantic issue: it affects whether the headline claim is empirically substantiated or interpretive. A more defensible framing would separate “evidence for repeated adaptation/convergence” from “evidence for high evolvability.” As written, the paper collapses these distinct concepts.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|GPT|2", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "This paper’s key convergence result (analogue vs non-analogue mean Procrustes distances) is not a robust test of evolutionary convergence because it depends on subjective analogue assignments and compares many non-independent pairwise distances without a clearly specified phylogenetically informed convergence framework; this weakens Validity and Conclusions for the “convergent evolution dominates phylogenetic history” claim.\n\n\"The average Procrustes distance between afrotherians and their non-afrotherian analogues (Fig. 1, Table 1) was 0.238, whereas the average distance between afrotherians and (non-afrotherian) non-analogues was 0.281. In other words, the average shape distance for pairs of non-analogues was 18.0% higher than for pairs of analogues (\\( p < 0.001 \\)), reflecting convergent evolution in Afrotheria and other mammals.\" \nThe paper interprets a difference in mean pairwise distances as evidence of evolutionary convergence, but this inference is sensitive to how “analogues” are chosen and how distances are aggregated. Pairwise distances are highly non-independent because each taxon contributes to many pairs, and means can be driven by a few extreme taxa (e.g., very distinctive outgroups or highly derived species). Moreover, “non-analogues” is a heterogeneous reference group that differs from “analogues” not only in ecology but also potentially in phylogenetic distance and sampling composition, which can affect mean Procrustes distances even under no convergence. Because the paper uses ecological/morphological criteria to define analogues, the test effectively evaluates whether ecological similarity correlates with ear shape similarity—this is informative, but it is not automatically equivalent to a convergence test under a formal comparative model. The conclusion “reflecting convergent evolution” is therefore stronger than what the statistic alone establishes.\n\"Significance tests of the H0 of equal average distances were based on permutation tests that permuted the affiliation of species across Afrotheria-analogue pairs.\" \nThis description leaves critical design choices unspecified, including what exactly is permuted (pair labels, analogue assignments, or species identities), how constraints are handled when some afrotherians have multiple analogues, and how many permutations were used. Because the statistic is an average over many dependent distances, standard permutation schemes can yield anticonservative p-values if the resampling unit is not chosen correctly. In addition, the analogue mapping itself encodes biological judgment, so a p-value from permuting affiliations may not correspond to a well-defined null model of “no convergence” under phylogeny. The paper also does not report sensitivity analyses (e.g., alternative analogue matchings, excluding outgroups, or controlling for phylogenetic distances) that would be common practice to demonstrate robustness. As a result, the reported p-value does not convincingly support the strength of the stated convergence conclusion.\n\"Briefly, the Wheatsheaf index generates phenotypic (Euclidean) distances from any number of traits across species and penalizes these by phylogenetic distance before investigating similarity (in order to weight close phenotypic similarity higher for distantly related species). It also takes an a priori designation of focal species, which are defined as species belonging to a niche for which the traits are hypothesized to converge.\" ([2](https://pmc.ncbi.nlm.nih.gov/articles/PMC4329985/))\nThis passage summarizes a standard rationale in convergence methodology: distance-based convergence assessments typically incorporate phylogenetic relatedness so that similarity among close relatives is not misread as convergence. The present paper’s main-text convergence statistic is based on mean Procrustes distances between analogue and non-analogue pairs, but it does not describe an explicit phylogenetic penalization of distances for that test, nor does it justify why a non-phylogenetic mean-distance comparison is sufficient. Because the paper’s conclusion contrasts “functional adaptation” against “phylogenetic history,” a method that explicitly partitions or penalizes phylogenetic similarity is particularly relevant. The cited description also emphasizes the importance of clearly defining focal taxa and the logic of the null model; in this paper, analogue definitions and permutation details are not sufficiently transparent to play that role. Consequently, the convergence evidence is less rigorous than what is common in phylogenetic convergence studies.\n\"The study of convergent evolution will be facilitated if researchers are explicit about working definitions of convergence and adopt a standard toolbox of convergence measures.\" ([3](https://pubmed.ncbi.nlm.nih.gov/26177938/))\nThis recommendation is directly applicable because the paper uses a bespoke distance-contrast between “analogues” and “non-analogues” as its primary convergence evidence. The paper does not clearly situate this statistic relative to established convergence metrics (e.g., lineages closing phenotypic distance, or phylogenetically explicit indices), and it does not articulate what process- or pattern-based definition is being used. Without that clarity, it is difficult to interpret whether the reported mean-distance difference captures convergence, shared ecology correlated with phylogeny, or sampling design effects. Adopting or benchmarking against a standard toolbox would help isolate the intended signal and improve interpretability. As written, the convergence claim is not supported with the level of methodological standardization suggested by the convergence literature.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|GPT|3", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "This paper’s identification of four “trait combinations” underlying convergence via 2B-PLS is not robustly justified because it interprets PLS axes (including a non-significant fourth axis) as functional/adaptive dimensions and then reuses those axes to demonstrate convergence, creating circularity and weakening Conclusions and Appropriate use of statistics for Figures 3–4 and the “four dimensions” claim.\n\n\"To identify the features that underlie this convergence in bony labyrinth shape, we performed a two-block partial least squares analysis (2B-PLS) between all 372 Procrustes shape coordinates and 12 contextual variables that capture multiple aspects of ecology and positional behaviour (Table 2).\" \nThis establishes that the latent variables are explicitly constructed to maximize covariance with the chosen contextual variables, not to maximize evidence of convergence per se. Consequently, interpreting these axes as the “features that underlie convergence” requires a careful argument that the contextual variables are valid and sufficiently complete proxies for the selective regimes that drive convergence. The paper later acknowledges missing direct auditory parameters, which makes the mapping from PLS axes to functional selection more uncertain. Additionally, the number of shape variables (372) is very large relative to the number of taxa (40), which increases the risk that latent-variable structure is sensitive to sampling and to correlated predictors. The paper provides qualitative descriptions of axes, but does not provide a rigorous uncertainty quantification for those axis interpretations beyond the reported p-values. This weakens the claim that the extracted axes uniquely “underlie” convergence.\n\"The first four dimensions (or pairs of latent variables) together accounted for 93.8% of the summed squared covariances between the two blocks of variables (hierarchical permutation tests against a null hypothesis of no association yielded \\( p \\)-values of 0.001, 0.030, 0.043, and 0.103, respectively, for the four dimensions).\" \nThe fourth dimension is not statistically supported under conventional thresholds (p = 0.103), yet the paper’s abstract and discussion emphasize “four trait combinations” as a core finding. If the hierarchical test is the basis for deciding which dimensions represent non-random association, then including a non-significant axis as an identified “trait combination” is not justified without additional rationale (e.g., corrected thresholds, preregistration, or strong prior hypotheses). Moreover, multiple dimensions are tested, but the manuscript does not describe how familywise error or false discovery is controlled (or why it is unnecessary) for these sequential inferences. Treating the first four axes as a settled set despite mixed statistical support can lead to overstated interpretation of patterns, especially when later steps depend on the choice of “four.” This directly affects the reliability of the “four combinations” conclusion.\n\"Given the importance of habitat and locomotor behaviour to a species’ morphological adaptations, the four PLS dimensions described above estimate the “functional” aspects of labyrinth shape ... When computed only from these four PLS dimensions, the average shape distance for pairs of non-analogues was even 42.0% higher than for pairs of analogues (\\( p<0.001 \\)) ... This indicates that the pattern of convergence is successfully captured by the four PLS dimensions.\" \nThis argument is potentially circular because the PLS dimensions are computed to maximize covariance with contextual variables that were chosen precisely to encode ecological/behavioral differences related to the analogue concept. Showing that distances computed in the subspace defined by these supervised axes amplify analogue/non-analogue separation does not independently validate that these axes are the causal “functional” dimensions; it may simply restate how PLS is constructed. An independent validation would typically involve out-of-sample prediction, sensitivity to alternative contextual codings, or benchmarking against direct functional measurements (e.g., audiograms) where available. The text also embeds strong causal language (“functional aspects”) that exceeds what covariance-maximizing latent variables can establish on their own. Therefore, the conclusion that four axes “successfully capture” convergence is not as robust as presented.\n\"One approach commonly used to characterize ahistorical patterns of morphological integration between blocks of traits is partial least squares (PLS). Partial least squares is a statistical procedure that quantifies the degree of covariation between sets of variables, based on the overall trait covariance matrix\" ([4](https://faculty.sites.iastate.edu/dcadams/files/inline-files/2014-plos1-adams-felice-phylomorphointegr_1.pdf)).\nThis description underscores that PLS is fundamentally a covariation summarization tool, not a direct estimator of functional adaptation or selection. The paper under review uses PLS axes to infer “functional” aspects of shape and to argue that convergence is “captured” by those axes, but such interpretations require additional evidence linking the contextual variables to causal selective pressures. Because PLS will always find axes of maximal covariation, strong variance-explained statements (e.g., 93.8% of squared covariance) can be misleading if interpreted as demonstrating biological primacy rather than statistical construction. The quoted methodological framing suggests that PLS is best treated as exploratory integration/covariation analysis unless coupled with independent validation. This directly challenges the strength of the “four trait combinations underlying convergence” conclusion as written.\n\"However, while this approach is appropriate for evaluating trends in one or a few traits, it is incapable of assessing patterns in highly multivariate data, as the large number of variables relative to sample size prohibits parametric test statistics from being computed.\" ([5](https://faculty.sites.iastate.edu/dcadams/files/inline-files/2014-evol-adams-dpgls.pdf))\nThis passage highlights a core statistical tension in comparative morphology: when dimensionality approaches or exceeds sample size, inference becomes fragile and can require specialized procedures and careful validation. Although 2B-PLS can be computed in high-dimensional settings, interpreting multiple latent axes as biologically meaningful “trait combinations” still demands strong safeguards against overinterpretation, particularly with N = 40 taxa and 372 shape variables. The paper provides qualitative axis descriptions and reports permutation p-values, but it does not demonstrate robustness to alternative model specifications (e.g., alternative contextual encodings, different landmark subsets, or leave-out strategies for the shape loadings themselves). The high-dimensional setting also motivates clearer reporting of uncertainty around axis stability and downstream statistics. Without such safeguards, the strength and number (“four”) of inferred functional trait combinations remain uncertain.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|GPT|4", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "This paper does not provide sufficient computational detail to reproduce its headline p-values and “hierarchical permutation test” results (for analogue vs non-analogue distances and per-dimension PLS significance), because the manuscript states that core analyses were performed in Mathematica while the provided R scripts omit the described permutation tests; this is a major Data and methodology flaw affecting reproducibility.\n\n\"The first four dimensions ... accounted for 93.8% ... (hierarchical permutation tests against a null hypothesis of no association yielded \\( p \\)-values of 0.001, 0.030, 0.043, and 0.103, respectively, for the four dimensions).\" \nThese p-values are central to the claim that there are four meaningful PLS dimensions, but the manuscript does not describe the hierarchical permutation procedure in enough detail to reproduce it (e.g., permutation scheme, number of permutations, stopping rules, and how hierarchy is enforced). Because different permutation schemes can yield materially different p-values in multivariate contexts, reproducibility requires explicit procedural specification. The paper also uses the p-values to justify interpretive focus, so inability to reproduce them affects the credibility of the “four dimensions” narrative. Without code or a precise algorithmic description, readers cannot validate whether these results are robust to implementation choices. This is a substantial reproducibility gap rather than a documentation nit.\n\"Significance tests of the H0 of equal average distances were based on permutation tests that permuted the affiliation of species across Afrotheria-analogue pairs.\" \nThis describes a custom permutation test but does not specify essential implementation details (what constitutes a permutation unit, whether analogue multiplicity is preserved, how shared taxa are handled, and how p-values are computed from the permutation distribution). In addition, the code provided with the paper (see below) does not implement this permutation test, so the reported p-values cannot be regenerated from the shared scripts. When a key result hinges on a nonstandard resampling scheme, it is common practice to provide code and explicit parameters because small differences can change significance conclusions. The lack of implementation detail prevents independent verification. This directly impacts the paper’s reproducibility and the reliability of its statistical claims.\n```r\n# ---- Average distances ----\n\n# Arithmetic mean\nmean(d.af_an)  # Afrotheria vs. non-Afrotheria analogues = 0.2445418\nmean(d.af_nan)  # Afrotheria vs. non-Afrotheria non-analogues = 0.2869142\nmean(d.af_af)  # Afrotheria only = 0.2663105\nmean(d.naf_naf)  # non-Afrotheria only = 0.2897568\n# Difference analogues / non-analogues\n(mean(d.af_nan) - mean(d.af_an))/mean(d.af_an)\n```\nThis excerpt from the shared analysis code computes means and effect sizes but does not compute the manuscript’s reported p-values for analogue vs non-analogue comparisons (e.g., the p < 0.001 claim in the main text). The absence of the described permutation test implementation means the reported significance is not reproducible from the provided scripts, even with the shared dataset. This is not a minor omission: statistical significance is used to support the convergence interpretation. If the authors relied on Mathematica for the permutation test, then the Mathematica code (or an equivalent implementation) is needed for transparency. Without it, readers cannot validate the numerical claim that the effect is statistically significant under the stated null.\n```r\n# 2B-PLS\nafro.pls <- pls2B(A.gpa$rotated, ECOL_std)  # analysis\n\n# Table of the proportion of covariance explained by each PLS dimension\nafro.pls$CoVar\n```\nThe shared R script performs 2B-PLS and reports variance-explained quantities, but it does not implement the hierarchical permutation tests described in the paper for per-dimension p-values. The script includes cross-validation plots for loadings and computes phylogenetic signal in PLS scores, which are useful diagnostics, but they do not substitute for the specific significance procedure the manuscript reports. As a result, a reader following the provided code cannot reproduce the p-values that justify interpreting the first four dimensions, including the claimed thresholding of “further dimensions.” This breaks the paper’s reproducibility chain between methods, code, and results. Given that these p-values are used to motivate the “four trait combinations” conclusion, the missing implementation is a major limitation.\n\"PCA, 2B-PLS, and shape visualisations were performed using the software Wolfram Mathematica 12.\" \nThis indicates that the key multivariate analyses producing the reported p-values and shape visualizations were executed in Mathematica, but no Mathematica notebook/script is provided in the accompanying materials here. In computational morphology papers, it is common to share the exact analysis scripts used to generate reported statistics, particularly for custom permutation procedures. Providing only partial re-implementations in another language can be sufficient if they reproduce all key results, but the provided R scripts do not do so for the reported p-values. Therefore, the stated computational provenance increases the need for sharing the Mathematica implementation. Without it, the analysis pipeline cannot be independently audited end-to-end.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|GPT|5", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "This paper’s reliance on a single specimen per species and heterogeneous scan sources/resolutions, without reporting landmarking/segmentation error or within-species variance, creates a substantial uncertainty in the Procrustes distance and PLS-based inferences; this weakens Conclusions and Data and methodology for the morphometric dataset and downstream statistics.\n\n\"We landmarked a single bony labyrinth per species.\" \nUsing one specimen per species can be defensible for very deep phylogenetic comparisons, but it requires explicit evidence that within-species variance and measurement error are negligible relative to between-species differences for the specific structures and landmark scheme used. Here, Procrustes distances and PLS scores are treated as species-level traits, so any unquantified specimen-level noise directly propagates into the key statistics. Because the paper’s central convergence claim depends on small differences in average distances and on interpreted multivariate axes, uncertainty from within-species variation can materially affect results. The paper does not present replicated landmarking, repeated segmentations, or measurement-error analyses that would quantify this uncertainty. This omission is important because it limits confidence in the precision of the reported distance contrasts and axis interpretations. A small pilot error study (even on a subset) would substantially strengthen reliability.\n\"We downloaded the microCT scans of 13 crania from MorphoSource ... with resolutions ranging from 7.88 to 82.67 μm ... We also scanned crania of 24 species ... with resolutions ranging from 7.13 to 106.67 μm ... For each specimen, we virtually extracted the surface of one bony labyrinth using the software Amira ...\" \nThis shows that the dataset combines scans from multiple institutions and acquisition pipelines with wide variation in voxel size and with at least one anisotropic scan (e.g., 93*93*200 μm) described elsewhere in the methods. Such heterogeneity can affect the precision of centerline extraction and semilandmark placement, especially for small or thin canal structures. In this setting, it is common to evaluate whether scanner type/resolution or processing choices induce systematic differences in landmark coordinates. The paper does not report any checks for scan-source effects or segmentation/landmarking repeatability across conditions. Because the analyses compare subtle shape differences across ecological regimes, unmodeled acquisition effects could bias or blur those patterns. This uncertainty is not addressed in the reported statistics.\n\"Hence, we did not consider within-species variation, sexual dimorphism, and bilateral asymmetry; instead we aimed to maximise taxonomic, phylogenetic, and ecological breadth of the sample.\" \nThe rationale given is plausible as a design choice, but it remains an assumption rather than a demonstrated property of the specific landmark dataset used here. Even if mean asymmetry is small, the relevant question for distance-based convergence tests is whether the magnitude of specimen-level noise is small relative to the analogue/non-analogue distance gap and to the PLS axis separations. The manuscript does not quantify that gap relative to plausible error bounds, so readers cannot assess whether the effect sizes are robust. Moreover, landmarking on complex 3D structures with semilandmarks can introduce observer-dependent variance. Without reporting repeatability, the reader must take on faith that specimen-level noise is negligible. This weakens confidence in the statistical interpretation of the morphometric results.\n\"Researchers should be cautious when compiling data from multiple methods and/or observers, especially if analyses are focused on intraspecific variation or closely related species, as in these cases, patterns among individuals may be obscured by interobserver and intermethod error. Conducting interobserver and intermethod reliability assessments prior to the collection of data is recommended.\" ([6](https://www.gc.cuny.edu/sites/default/files/2021-12/Robinson-and-Terhune-2017-error-paper.pdf))\nWhile this guidance is framed around intraspecific and closely related taxa, it captures a general principle directly relevant here: heterogeneous acquisition/processing pipelines and landmarking choices can introduce error that affects multivariate morphometric patterns. This paper’s dataset spans many taxa and uses multiple scan sources and resolutions, which is precisely a scenario where intermethod differences could enter the analysis unnoticed. The authors’ choice of one specimen per species removes the possibility of estimating within-species variance from the collected sample, increasing reliance on measurement reliability. The cited recommendation indicates that a reliability assessment is a standard safeguard when combining heterogeneous data sources. Without such an assessment, it is difficult to bound uncertainty in pairwise distances and PLS scores. Therefore, the paper’s conclusions would be strengthened by explicitly quantifying these errors.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "The sample size (N=40) is critically small compared to the number of variables (372 shape coordinates + 12 contextual variables), which likely leads to overfitting and spurious correlations in the Two-Block Partial Least Squares (2B-PLS) analysis.\n\n\"The sample consists of 20 Afrotheria and 20 non-afrotherian mammals considered to be their “analogues”.\"\nA sample size of 40 is extremely low for a geometric morphometric analysis involving 124 landmarks (372 coordinates). In high-dimensional data analysis, when the number of variables far exceeds the number of observations, statistical methods like PLS maximize covariance by exploiting random noise, leading to inflated correlation coefficients and unstable axes.\n\"The first four dimensions (or pairs of latent variables) together accounted for 93.8% of the summed squared covariances\"\nThis exceptionally high percentage of explained covariance is a hallmark of overfitting in PLS with small sample sizes. It suggests that the analysis is capturing idiosyncratic variation specific to this small sample rather than robust biological patterns.\n\"To identify the features that underlie this convergence in bony labyrinth shape, we performed a two-block partial least squares analysis (2B-PLS) between all 372 Procrustes shape coordinates and 12 contextual variables\"\nIncluding all 372 coordinates directly in the PLS without prior dimensionality reduction (e.g., using PC scores) exacerbates the \"curse of dimensionality\".\n\"Over the years, research has shown how the number of variables used in Geometric Morphometrics can be problematic for studies using small sample sizes.\" [1]\nThis literature highlights that insufficient sample sizes in geometric morphometrics can lead to unstable and non-replicable results, particularly when using multivariate methods like PLS that are sensitive to the ratio of variables to specimens.\n\nReferences:\n[1] Cardini, A. (2019). Sample size and sampling error in geometric morphometric studies of size and shape. *Zoomorphology*, 139, 517-532. https://link.springer.com/article/10.1007/s00435-020-00495-z", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "The analysis treats ordinal contextual variables (e.g., agility scores 1-6, aquatic scores 1-4) as continuous data in the PLS analysis, which violates the assumptions of the method and distorts the relationships between shape and ecology.\n\n\"The contextual variables were mean-centred and scaled to unit variance.\"\nCentering and scaling (standardizing) is a procedure for continuous variables. Applying this to ordinal data assumes that the intervals between categories (e.g., between \"slow\" and \"medium slow\") are equal, which is rarely true for ecological rankings.\n\"Agility... 1 = extra slow, 2 = slow, 3 = medium slow, 4 = medium, 5 = medium fast, 6 = fast\"\nThese categories represent a rank order, not a linear scale. Treating them as continuous forces a linear relationship where none may exist, potentially masking non-linear associations or creating spurious linear ones.\n\"afro.pls <- pls2B(A.gpa$rotated, ECOL_std)\"\nThe code confirms that the standardized ordinal matrix `ECOL_std` is passed directly to the `pls2B` function, which computes the singular value decomposition based on covariance, a measure appropriate for continuous data.\n\"There are two options for PLS analysis: between two separate blocks, or between blocks within a configuration of landmarks.\" [2]\nStandard PLS implementations in morphometrics software typically assume continuous variables in both blocks. Using ordinal data requires specific adaptations (e.g., categorical PLS or rank-based methods) which were not employed here.\n\nReferences:\n[2] Klingenberg, C. P. (2011). MorphoJ: an integrated software package for geometric morphometrics. *Molecular Ecology Resources*, 11(2), 353-357. https://onlinelibrary.wiley.com/doi/10.1111/j.1755-0998.2010.02924.x", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "The conclusion that the mammalian inner ear possesses \"high evolvability\" is an overstatement, as the study only demonstrates convergence (the *occurrence* of evolution) without a comparative framework to assess the *capacity* (evolvability) relative to other groups or traits.\n\n\"Convergent evolution in Afrotheria and non-afrotherians demonstrates high evolvability of the mammalian inner ear\"\nConvergence shows that a trait *has* evolved in response to similar pressures, but it does not quantify the *potential* to evolve (evolvability). A trait could be highly constrained but still converge if the selection pressure is strong enough and the path of least resistance is shared.\n\"The high evolvability of the mammalian ear is surprising: nowhere else in the skeleton are different functional units so close together\"\nThis claim implies a comparison (\"high\" relative to what?), yet the study does not compare the rate or magnitude of evolution of the inner ear to other skeletal traits or to the inner ears of non-mammalian vertebrates.\n\"Evolvability is the ability of a population to produce variants of higher fitness.\" [3]\nEstablishing \"high\" evolvability requires demonstrating that the inner ear produces adaptive variation more readily than other systems, which this study's design (focusing on pattern matching) cannot address.\n\nReferences:\n[3] Wagner, G. P., & Altenberg, L. (1996). Perspective: Complex adaptations and the evolution of evolvability. *Evolution*, 50(3), 967-976. https://academic.oup.com/evolut/article/50/3/967/6752180", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "The selection of \"analogue\" species is based on subjective criteria rather than a systematic or quantitative approach, which introduces bias and potentially circularity if the selection criteria are correlated with the inner ear morphology.\n\n\"Analogues were identified based on their overall body morphology (e.g., the greater hedgehog tenrec, Setifer setosus, and the true hedgehog, Erinaceus europaeus), specific morphological traits... or locomotion and habitat\"\nThis selection process is qualitative and lacks reproducibility. Different researchers might choose different analogues. If \"overall body morphology\" is correlated with inner ear shape (due to shared developmental or functional constraints), then finding convergence in the inner ear is a trivial consequence of the sample selection.\n\"The sample was carefully composed based on... the ability of our team to acquire high-resolution micro-CT scans of the desired taxa.\"\nWhile practical constraints are understandable, they further limit the systematic nature of the sampling. A more robust approach would be to sample a broad range of mammals and test if those with similar ecologies converge, rather than pre-selecting pairs expected to converge.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Gemini|5", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "The interpretation of cochlear shape changes as adaptations for hearing is speculative because the study lacks direct physiological hearing data and relies entirely on habitat as a proxy, ignoring other potential drivers of cochlear variation.\n\n\"Data that directly measure auditory capacity could unfortunately not be included because common parameters of hearing ability... were unknown for many species in the sample.\"\nThe authors acknowledge this limitation but proceed to interpret cochlear shape variations (e.g., number of turns, radii) as direct functional adaptations for hearing sensitivity or frequency range.\n\"However, habitat type (e.g., aquatic, subterranean, or ground-dwelling) carries information about the medium through which species detect sound and may thus indirectly also reflect basic aspects of hearing.\"\nThis is a strong assumption. Habitat is a coarse proxy. Two species in the same habitat might have very different hearing strategies (e.g., one uses high-frequency communication, the other low-frequency detection of predators).\n\"The influence of cochlear shape on low-frequency hearing.\" [4]\nWhile previous studies have linked shape to function, applying these general associations to specific species without direct physiological data can lead to \"just-so stories\" where every shape change is interpreted as adaptive for a presumed function.\n\nReferences:\n[4] Manoussaki, D., Chadwick, R. S., Ketten, D. R., Arruda, J., Dimitriadis, E. K., & O'Shaughnessy, J. T. (2008). The influence of cochlear shape on low-frequency hearing. *Proceedings of the National Academy of Sciences*, 105(16), 6162-6166. https://www.pnas.org/doi/abs/10.1073/pnas.0710037105", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "Secondly, the main conclusion \"that functional adaptation and convergence dominate over phylogenetic history\" in placental mammals is not an unexpected result. Since the advent of DNA based phylogenetics, it has become quite clear that adaptation-drive convergent evolution was the main driver of mammalian phylogeny. Convergent evolution in the ear region of afrotherians has been discussed previously in Benoit J., Merigeaud S. and Tabuce R. (2013) Homoplasy in the ear region of Tethytheria and the systematic position of Embrithopoda (Mammalia, Afrotheria). Geobios, 46(5): 357-370.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "Missing some crucial papers about convergent evolution in the Afrotherian ear: Benoit 2013 (embrithopods and convergence with elephants) / Benoit 2013 on sirenians (and convergence with cetaceans)", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "Using the provided landmarks, I have tested your dataset using hierarchical analyses to see morphological proximities (.nex file resulting provided here). I was very surprised that Amblysomus/Chrysochloris cluster with Talpa/Cryptomys and also Hemicentetes/Setifer/Tenrec with Erinaceus that clearly indicating for sure something maybe ecological. I was unfortunately unable to observe other grouping for ecology but “just” phylogenetic natural clades, especially Afrotherians (hyrax, Chrysochloridae, Tenrecidae, Macroscélides, Sirenia). Then I am wondering if the sampling should be more extensive. Indeed, when including 20 species from the super-order Afrotheria, you see a clear phylogenetical signal. What would happen if you add more from the 5 other super-order considered in this study? This has also been demonstrated in Cetaceans that increasing the number of species, noise that was first interpreted as an ecological signal is lost. In the case of Cetaceans, only extreme divers (more than 2000 meters) have a convergent evolution of the cochlea (Parks et al. 2019).", "reviewer_type": "human", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|68|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "The ecological aspect of the bony labyrinth has been several time challenged lately using large datasets (Benoit et al. 2020, Araujo et al. 2022, David et al. 2022, Evers et al. 2022, Mennecart et al. 2022) and soft tissues may be necessary to obtain ecological parameters (David et al. 2016). Metabolism (mammaliaforms), neutral evolution (ruminant), skull configuration (bird), and allometry (turtle) may be the most important factors that shape evolution after these authors. How would you consider your results in the light of these researches? Considering your 3 first PLS (the 4th has a p.value of more than 0.05 and not significant, right?), I would like to discuss and understand the results.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "Among your outliers, your first one is the dolphin. I would advise to delete this specimen because your dataset is not normalized due to this specimen (or include transition forms from land to sea in cetacean lineage to normalize). Including the dolphin that is so different may attract and bias the ecologically/shape for the aquatics. Then after deleting this specimen, please retest your dataset to see if the reduction of the canals is still observed and not biased by this specimen.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "Considering PLS2, you indicate the angle between the anterior and the posterior canals and a narrow cochlea for fossorial behavior. This is very interesting. The platypus is put as a semi-aquatic but also dig nests. Moreover, Mennecart et al. 2022 (and other papers of them), use these characters for phylogeny and family splitting in ruminants. Tragulidae are in graph 3F the closest to the vole. However, they have these morphological characteristics since at least the Early Miocene with different ecologies and environments depending of the species. They are not known to dig. Are all the ecological categories well-defined?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "Why did you prefer to have in the text the analysis with phylogenetical component and in the supplementary the one that take into account for phylogeny?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "Chrysochlorys and Ochotona are also outliers. Indeed their shape are strange. Are the entire bony labyrinths in open access to verify the original shape?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "L35. Size, Costeur et al. 2017 demonstrated that the allometry of the BL is clearly minor. A shrew has a 5mm BL while a whale has a 3cm BL. This is related to the fact that this is the first organ to ossify around mid-gestation (Mennecart & Costeur 2016, Costeur et al. 2018, and others).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Human_2|10", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "L37. The head posture has been challenged by Benoit et al. 2020. They found that the head posture is correlated to the phylogeny and the canals also, but the orientation of the canals cannot predict the head posture.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Human_2|11", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "L53 “high disparity to diversity ratio” do you mean today? In comparison to what? To each super-order considered in the analysis? All mammal species?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Human_2|13", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "Figure 1 is difficult to read and we miss all the ecological parameters. Maybe you could add the 8 contextuals to this figure using colors instead of 1, 2, 3 right after the name in the phylogeny and under use the animal outlines in pair with their analogues forming the 12 groups of Afrotheres and analogues.", "reviewer_type": "human", "label": "error", "error_type": "Neglect", "label_origin": "expert+llm-filter"}
{"id": "prb|68|Human_2|15", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "L151-155. The p.value is not significant. Maybe you should delete this part.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Human_2|16", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "L158 how different is it? What the impact of the phylogeny here?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Human_2|17", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "L191-197 references are missing.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Human_2|18", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "L198 instead of very small -> significantly smaller", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Human_2|19", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "L202 mammals have", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Human_2|20", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "L202 limited number of turns, how many?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Human_2|23", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "L243-246 references are missing.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Human_2|24", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "L263-264 this has actually been done in Evers et al. 2022", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Human_2|25", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "L282 what is high resolution? Usually this is between 40 and 60 micro.", "reviewer_type": "human", "label": "error", "error_type": "Neglect", "label_origin": "expert+llm-filter"}
{"id": "prb|68|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "The first result presented is the Procrustes distances between all pairs of afrotherians and non-afrotherians. These data are discussed as averages: \"The average Procrustes distance between afrotherians and their non-afrotherian analogues was 0.238, whereas the average distance between afrotherians and (non-afrotherian) non-analogues was 0.281.\" Fron these data, the authors conclude that \"functional adaptation dominates over phylogenetic history.\" I'm assuming that Procrustes distance was measured for each category (ground-dwelling, aquatic, etc) and then the authors made an average. However, these data should be presented per category in table form. It seems clear from Figs. 3,4 that some categories are more disparate than others and even may not be statistically different. In that regard, it would be notable which functional categories overlap and which are distinct.", "reviewer_type": "human", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|68|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "The data in Figs. 3,4 and Fig. S3 do not appear to show analyses for significance or variance. In the text describing these figures, shapes are described morphologically, but not quantitatively. The authors do discuss statistics for phylogenetic signals, but such statistical analyses are missing from the adaptive signals. Some of the adaptive dimensions are clearly better at separating the groups, and this could be discussed if it is statistically supported. The ground-dwelling groups occupy a lot of shape space, which could also be a point of discussion.", "reviewer_type": "human", "label": "error", "error_type": "Neglect", "label_origin": "expert+llm-filter"}
{"id": "prb|68|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "Only one image of the bony labyrinth is shown. It would be more convincing to see a representative image of a bony labyrinth from each of the major eco-types. This is especially important given the amount of discussion in the text relevant to the shapes.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "The authors conclude that 1) the mammalian ear exhibits “high evolvability,” 2) that this is surprising because the bones are small and close together, and 3) the evolvability is a direct direct consequence of the increased genetic and developmental complexity of the mammalian ear compared to other vertebrates.” All of these conclusions seem a bit tenuous to me. “Evolvability” as a character trait is not evaluated. I think the authors are suggesting that the bony labyrinth exhibits a lot of morphological variation compared to other structures, but they have not actually quantified that. The authors also imply that because the mammalian middle ear consists of more elements than the avian middle ear and/or because it consists of both first and second pharyngeal arch components that it is more genetically complex than the avian middle ear, but in fact, there is no evidence for that. Avian mandibles consist of more bones than the mammalian mandible, but I don’t think anyone would suggest the avian mandible is genetically more complex than the mammalian mandible. It may rather be that the pharyngeal arches (notably PA1 and PA2) have developmental mechanisms that contribute to evolvability which may impact any or all of their derivatives which are quite variable among vertebrates. Since the authors do not present any genetic or developmental data, nor do they evaluate other characters within mammals or ear structures in any other clades, these comparative statements seem unwarranted.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|68|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb68", "comment": "In lines 31-34, the authors state: “We previously proposed that this increased heterogeneity and developmental complexity of the mammalian ear bestows it a higher evolvability, i.e., an enhanced capacity for adaptive evolution, and that this increase in evolvability likely contributed to the evolution of the spectacular disparity in mammalian body plans and ecological niches.” This also seems a bit of an overstatement. As mentioned above, developmental complexity of the mammalian ear is not shown, but linking evolvability of the middle ear would to disparity of body plans is a big leap.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|69|Claude|1", "source": "prb", "split": "test", "paper_id": "prb69", "comment": "The paper's central claim linking transposon abundance to susceptibility to environment-induced heritable changes is based solely on correlational evidence from only 6 genotypes, without experimental validation of a causal mechanism.\n\n\"To explore which factor predicted the susceptibility of a genotype to environmental induction, we regressed the occurrence frequency of genotypes against different explanatory variables (climate of origin, methylation levels, and transposon abundance) and found that the abundance of transposons in the Gypsy (r = -0.840) and MuDR (r = 0.815) superfamilies explained a significant proportion of the variation (Fig. 3b, Extended Data Fig. 3b).\"\nThe correlations reported (r = -0.840 and r = 0.815) are calculated from only 6 genotypes, as stated later in the Methods. With such a small sample size, statistical power for correlation analysis is severely limited, and the correlations are highly susceptible to being driven by one or two outlier genotypes. According to standard statistical guidelines, a sample size of n=6 provides 80% power to detect only extremely large correlations (r > 0.80 at α = 0.05), and the resulting confidence intervals would be extraordinarily wide (approximately 0.33 to 0.99 for r = 0.9), providing minimal useful information about the true effect size [[1]](#ref1).\n\"These data were available for seven genotypes, including Abd-0, Ang-0, Col-0, Dja-1, Sap-0, Tol-0, and Ws-2 (Supplementary Table 1). The transposon data of Col-0 were not included in the subsequent analysis because Col-0 is the reference genome and shows biased (much more detailed) annotation of transposons compared to other genotypes.\"\nThe exclusion of Col-0 reduces the already limited sample to just 6 genotypes for the transposon correlation analysis. This sample size is far below the minimum recommended for correlation studies. Standard guidelines suggest sample sizes of at least 30-50 for moderate correlations, and this limitation severely undermines the reliability of the paper's key finding that transposon abundance predicts susceptibility to environmental induction [[2]](#ref2).\n\"These results indicate that transposons play a central role in mediating environment-induced changes, which could occur through epigenetic modifications of transposons (i.e., DNA methylation and RNA interference) that simultaneously regulate the expression of downstream genes or through de novo transposon insertions that alter gene expression patterns.\"\nThis statement suggests potential mechanisms but none were experimentally tested. The paper provides no evidence of differential DNA methylation at transposon sites, no measurement of siRNA changes, and no detection of de novo transposon insertions in the experimental lines. Without mechanistic validation, the correlational evidence cannot support the strong conclusion that transposons \"play a central role\" in mediating these effects.\n\nReferences:\n[1] [Sample Size and Power for Correlation Analysis - Portland State University](https://web.pdx.edu/~newsomj/mvclass/ho_sample%20size.pdf)\n[2] [An elaboration on sample size determination for correlations based on confidence interval estimation](https://pmc.ncbi.nlm.nih.gov/articles/PMC11148401/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|69|Claude|2", "source": "prb", "split": "test", "paper_id": "prb69", "comment": "While the paper claims that environment-induced heritable changes are common and implicates epigenetic mechanisms, no direct measurements of DNA methylation or histone modifications were performed on the experimental plant generations, leaving the mechanistic basis for inheritance entirely untested.\n\n\"The raw methylation data of 14 genotypes were obtained from published sources.\"\nThe DNA methylation data used in this study were not generated from the actual experimental plants that underwent environmental treatments, but rather from previously published data for the original genotypes. This means the study cannot determine whether epigenetic marks actually changed in response to ancestral environments or whether such changes were transmitted to offspring generations. This is a critical limitation because demonstrating transgenerational epigenetic inheritance requires showing that epigenetic marks change in response to environmental treatment and persist across generations [[3]](#ref3).\n\"Our study thus challenges the classic view that the environment only participates in the selection of heritable variation and suggests that the environment can broadly contribute to the generation of heritable variation.\"\nThis strong conclusion about the environment generating heritable variation implies an epigenetic mechanism, yet the study only measured phenotypes and gene expression, not the epigenetic modifications themselves. As emphasized in the literature on transgenerational epigenetic inheritance, establishing causality requires direct measurement of epigenetic marks and demonstration that they escape meiotic reprogramming to be transmitted across generations [[4]](#ref4).\n\"These de novo heritable variations may arise from the mechanisms discussed earlier, including epigenetic changes (DNA methylation, histone modifications, and small interfering RNAs) or de novo insertion of transposons.\"\nThe paper lists multiple possible mechanisms but tests none of them directly. Without measuring DNA methylation, histone modifications, siRNAs, or transposon insertions in the actual experimental lines across generations, the study cannot distinguish between true epigenetic inheritance and other explanations such as cryptic genetic variation, maternal provisioning effects, or environmental microvariation [[5]](#ref5).\n\nReferences:\n[3] [Transgenerational Epigenetic Inheritance: myths and mechanisms - Cell](https://pmc.ncbi.nlm.nih.gov/articles/PMC4020004/)\n[4] [Molecular mechanisms of transgenerational epigenetic inheritance - Nature Reviews Genetics](https://www.nature.com/articles/s41576-021-00438-5)\n[5] [A critical view on transgenerational epigenetic inheritance in humans - Nature Communications](https://www.nature.com/articles/s41467-018-05445-5)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|69|Claude|3", "source": "prb", "split": "test", "paper_id": "prb69", "comment": "The paper defines heritable differentially expressed genes (DEGs) as those differentially expressed \"for at least two generations,\" but this definition does not distinguish true transgenerational epigenetic inheritance from intergenerational effects, genetic changes, or maternal effects.\n\n\"A gene was considered to be a heritable DEG if it was significantly differentially expressed for at least two generations.\"\nThis definition is problematic because expression changes detected in two consecutive generations (F1 and F2) could result from intergenerational effects (where the F2 germ cells were directly exposed to the ancestral environment in the developing F1 embryo) rather than true transgenerational inheritance. The field distinguishes between intergenerational effects (affecting F1 and potentially F2) and transgenerational effects (appearing in F3 or beyond for exposures during pregnancy), as the germline of F2 offspring was present in utero during the original F1 exposure [[6]](#ref6).\n\"Transgenerational Epigenetic Inheritance (TEI) describes the phenomenon that phenotypic traits... can be transferred to offspring generations via epigenetic mechanisms.\"\nAccording to established definitions in the field, true transgenerational epigenetic inheritance requires transmission of epigenetic information through the germline across generations that were never directly exposed to the original stressor [[6]](#ref6). For plants where seeds develop on the stressed maternal plant, F1 seeds are directly exposed, and the germ cells that will form F2 are exposed during F1 development. Thus, effects must persist to F3 or beyond to be considered truly transgenerational, making the \"two generation\" threshold used in this study insufficiently stringent.\n\"We found that all environmental treatments caused heritable phenotypic and gene expression changes, with a substantial proportion stably transmitted over all observed generations.\"\nWithout ruling out alternative explanations such as de novo genetic mutations, standing genetic variation inadvertently selected by the treatments, or maternal provisioning effects (seed quality/size differences), the claim that these changes represent environment-induced heritable variation through epigenetic mechanisms is not adequately supported. The paper acknowledges seed-mediated effects are possible but does not control for them [[7]](#ref7).\n\nReferences:\n[6] [Present and future challenges for the investigation of transgenerational epigenetic inheritance - Environment International](https://www.sciencedirect.com/science/article/pii/S0160412023000491)\n[7] [Effects of Multi-Generational Stress Exposure and Offspring Environment on the Expression and Persistence of Transgenerational Effects in Arabidopsis thaliana - PLOS ONE](https://journals.plos.org/plosone/article?id=10.1371/journal.pone.0151566)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|69|Claude|4", "source": "prb", "split": "test", "paper_id": "prb69", "comment": "The paper acknowledges significant phenotypic variation between offspring generations grown in different batches under ostensibly uniform conditions, creating a confounding factor that undermines the interpretation of transgenerational effects in the primary experimental data (Test I).\n\n\"why did some significant phenotypic changes disappear in one generation but reappear in the next (Fig. 2b), and why did the occurrence frequency of induced changes vary between offspring generations (Fig. 3a)? A potential explanation is that the growth conditions differed between offspring generations, as evidenced by significant phenotypic variation between generations in the control group (Extended Data Fig. 2c, Supplementary Table 3).\"\nThe authors acknowledge that control plants showed significant phenotypic variation between generations, indicating that growth conditions were not truly uniform across the different time periods when F1-F4 plants were grown. This environmental heterogeneity directly confounds the ability to attribute observed phenotypic differences to transgenerational inheritance rather than to differential responses to varying growth conditions.\n\"To eliminate the influence of variable growth conditions, we conducted a second test of ancestral treatment effects (Test II), where we selected a subset of 10 genotypes and five treatments and grew F1 to F4 plants together under the same conditions.\"\nWhile Test II was designed to address this limitation, it used only a subset of genotypes (10 of 14) and treatments (5 of 10), meaning the primary conclusions of the paper still rely heavily on Test I data, which is compromised by environmental confounding. The paper does not quantify how much of the variance in Test I could be attributed to environmental variation versus true transgenerational effects.\n\"Such variation may also contribute to the inconsistent effect sizes observed between generations (significant G × A.E × F, Supplementary Table 4).\"\nThe significant three-way interaction between genotype, ancestral environment, and generation (G × A.E × F) could be interpreted as evidence for complex transgenerational effects, but it could equally reflect differential genotype responses to the environmental variation between generations. Without a properly controlled experimental design where all generations are grown simultaneously from the start, distinguishing these explanations is not possible [[8]](#ref8).\n\nReferences:\n[8] [Transgenerational response to stress in Arabidopsis thaliana - PMC](https://pmc.ncbi.nlm.nih.gov/articles/PMC3115178/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|69|Claude|5", "source": "prb", "split": "test", "paper_id": "prb69", "comment": "The analysis of transposon enrichment near heritable DEGs relies exclusively on the Col-0 reference genome annotation, which the authors acknowledge may not accurately represent transposon distributions in other genotypes, potentially biasing the enrichment results.\n\n\"We adopted the transposon annotation of TAIR10 and performed the analysis using a customized script coded with R package 'GenomicRanges' v.1.42.0. Notably, our study adopted Col-0 as the reference, and genotype-specific genome assembly is necessary for a comprehensive understanding of this nonrandom phenomenon.\"\nThe authors use the TAIR10 transposon annotation (based on the Col-0 reference) to analyze transposon enrichment near DEGs across all four genotypes (Abd-0, Ang-0, Tol-0, TRE-1) in the RNA-seq analysis. Transposon insertion polymorphisms are extensive among Arabidopsis accessions, with different genotypes harboring unique insertions not present in Col-0 and lacking insertions present in Col-0. Using the Col-0 annotation for non-Col-0 genotypes will systematically miss genotype-specific transposons and incorrectly assign Col-0-specific transposons to regions where they may not exist [[9]](#ref9).\n\"The transposon data of Col-0 were not included in the subsequent analysis because Col-0 is the reference genome and shows biased (much more detailed) annotation of transposons compared to other genotypes.\"\nThis statement acknowledges that transposon annotation quality differs between the reference (Col-0) and other genotypes, yet the same reference annotation is used for the DEG-transposon enrichment analysis. The inconsistency in annotation quality across genotypes could create spurious enrichment signals or mask true associations, undermining the conclusion that heritable DEGs have higher transposon abundance in their upstream and gene body regions.\n\"We found that the abundance of members of several superfamilies, including Gypsy, HAT, Mariner, and Helitron, upstream and body of these susceptible genes was significantly higher than that of background genes (Extended Data Fig. 10b).\"\nThis finding relies on accurate mapping of transposons to gene regions across different genotypes. Given that the analysis uses only Col-0 transposon coordinates while the DEGs were identified from four different genotypes (Abd-0, Ang-0, Tol-0, TRE-1), the enrichment calculation conflates genomic coordinates that may not be equivalent across accessions due to structural variation. Genotype-specific genome assemblies, as the authors note would be needed, are essential to accurately test this hypothesis [[10]](#ref10).\n\nReferences:\n[9] [Genetic and environmental modulation of transposition shapes the evolutionary potential of Arabidopsis thaliana - Genome Biology](https://genomebiology.biomedcentral.com/articles/10.1186/s13059-021-02348-5)\n[10] [Transgenerational epigenetic inheritance in plants - PMC](https://pmc.ncbi.nlm.nih.gov/articles/PMC4359895/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|69|GPT|1", "source": "prb", "split": "test", "paper_id": "prb69", "comment": "This paper overstates a causal conclusion that ancestral environments broadly generate heritable (including *de novo*) variation, because the experimental design and measurements do not rule out DNA-sequence-based explanations (cryptic genetic variation, selection among residual variants, or stress-induced mutations/TE insertions) for the observed multigenerational differences.\n\n“Our work challenges the textbook understanding that environments are only involved in the selection of heritable variation\\(^{3}\\) and suggests that environments are broadly involved in the generation of heritable variation.”\nThis sentence makes a strong causal claim about the *origin* of heritable variation, not merely about transgenerational plasticity or parent-of-origin carryover. Demonstrating such a claim typically requires separating environmentally induced *non-genetic* inheritance from DNA sequence changes and selection on standing variation, which is difficult in multigenerational experiments. The manuscript primarily reports phenotype and expression differences, but it does not provide direct evidence that treated lineages remain genetically identical to controls across generations. Without genotyping/whole-genome sequencing (or other strong genetic controls) it is not possible to attribute persistent differences uniquely to environment-induced heritable (epigenetic) mechanisms. This matters because the paper explicitly discusses genetic mechanisms (e.g., TE insertions) that would change DNA sequence and therefore are not distinguishable from selection/mutation without genomic assays. The conclusion therefore exceeds what the described measurements can validate.\n“*de novo* heritable variations caused by environmental changes can serve as another primary source for rapid adaptation.”\nFraming the observed effects as *de novo heritable variations* implies new heritable variants are being created by the treatments, which is a much stronger claim than “ancestral environments influence offspring phenotypes.” The manuscript does not present direct evidence of new variants (e.g., newly arising TE insertions, de novo mutations, or stable epialleles that are shown to be independent of DNA sequence). In the absence of genetic validation, persistent lineage differences could reflect selection among any residual within-accession variation or rare mutations accumulating over seven generations, especially under stressful treatments. This is particularly relevant because the paper later proposes *de novo* TE insertions as a plausible mechanism, which would require genomic evidence to support. Common practice in epigenetic-inheritance work is to explicitly exclude DNA sequence change when making strong claims about epigenetic causality. As written, the paper’s causal interpretation is underdetermined by the presented evidence.\n“In the second generation, seeds of the four resulting plants were pooled for each genotype to establish the ancestral generation.”\nPooling seeds across multiple parental plants creates a mixture of lineages at the start of the “ancestral generation,” which can complicate causal attribution if any residual heterogeneity (or contamination) exists within the accession seed stock. Even in a predominantly selfing species, residual heterozygosity and within-stock variation are not impossible, and pooling makes it harder to ensure strict genetic identity across subsequent treated and control lines. If the ancestral treatments alter survival or fecundity, selection could act on whatever variation exists in the pooled population, producing heritable differences that are genetic rather than epigenetic. The manuscript does not report genotyping to confirm that treated and control descendants remained genetically matched. This weakness directly impacts the interpretation that the environment *generated* heritable variation, rather than sorting it. The design choice therefore creates a plausible alternative explanation that is not excluded.\n“In the ancestral generation, 26 out of 1008 (2.58%) lines died before seed production, and their offspring generation was replaced with seeds of a randomly selected replicate from the same genotype and treatment.”\nReplacing dead lines with seeds from other replicates breaks strict line continuity and can blur the mapping between a particular ancestral individual and its descendants. Even if the replacement rate is relatively small, it introduces an additional mechanism by which “line” identities (and thus heritable trajectories) can be reassigned, which complicates claims about stable transmission within a lineage. This matters because the paper interprets persistence across generations as evidence of heritability and stability, but the replacement procedure can effectively merge replicate histories. Such merging can inflate apparent persistence (by substituting a successful replicate’s seed for a failed replicate) and complicate statistical independence assumptions in downstream analyses. The manuscript does not quantify how these replacements affect specific treatment–genotype combinations, which could be nonrandom under stress. Without careful accounting, this weakens causal claims about stable inheritance arising from the treatment itself.\n“However such studies often concern inter- rather than trans-generational effects (Figure 1) and rarely exclude DNA sequence changes as the underlying cause for heritability.” [[1]](https://pmc.ncbi.nlm.nih.gov/articles/PMC4020004/)\nThis statement from a widely cited review highlights a core methodological standard: strong claims of transgenerational epigenetic inheritance require excluding DNA sequence changes as the cause. The paper under review makes broad claims about the environment’s role in generating heritable variation, but it does not provide genetic evidence to exclude DNA-sequence-based mechanisms. The review also emphasizes the frequency of confounding in studies that do not isolate truly transgenerational effects or that do not control for alternative explanations. Because the present manuscript explicitly invokes mechanisms that include *de novo* TE insertions, the need to separate sequence change from epigenetic inheritance is especially acute. Without such controls, the causal direction (“environment generates heritable variation”) remains ambiguous. This directly challenges the validity of the manuscript’s strongest conclusion.\n\nReferences:\n[1] [Heard E, Martienssen RA. Transgenerational Epigenetic Inheritance: myths and mechanisms. *Cell* (2014).](https://pmc.ncbi.nlm.nih.gov/articles/PMC4020004/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|69|GPT|2", "source": "prb", "split": "test", "paper_id": "prb69", "comment": "This paper’s key conclusion that environment-induced heritable phenotypic changes are common across environments is not statistically robust because “occurrence” is defined by repeated nominal significance tests (P<0.05) converted into binary outcomes without a multiple-comparisons strategy, creating a high risk of false positives in a very large testing problem.\n\n“we transformed the quantitative estimates of effect sizes into qualitative assessments, defining an environment-induced change as occurring when the effect size significantly deviated from zero.”\nThis sentence shows that the central “occurrence” metric is driven by whether each estimated effect size crosses a significance threshold. In a setting with many genotype × treatment × generation × trait combinations, repeated hypothesis testing at a nominal alpha produces false positives by construction. The manuscript does not describe a correction across the full family of tests used to declare changes, even though the downstream narrative relies on counting how often “significant” effects occur across generations and environments. Converting continuous effect estimates into binary significance further amplifies sensitivity to arbitrary thresholds and sample-size differences, which can distort prevalence claims. Because the conclusion “common across various environments” is built on these counts, statistical calibration of the error rate is essential. Without it, the reported prevalence can be substantially inflated.\n“According to these significances, we converted the effect sizes to qualitative occurrence data, where significant effect sizes were assigned a value of one, and nonsignificant effect sizes were assigned a value of zero.”\nThis explicitly confirms the binarization pipeline: multiple model coefficients are tested and then discretized into 0/1 outcomes. Such discretization throws away magnitude information and makes the analysis hinge on whether P-values fall just above or just below 0.05, which is known to be unstable across repeated sampling. More importantly, the manuscript does not specify any global false-positive control across the many coefficients tested across traits, treatments, and generations. In multigenerational, multi-factor designs, it is standard to either pre-specify a limited set of primary tests or apply family-wise/FDR control for discovery-style counting arguments. Here, the occurrence frequency and claims about “all environments” depend on aggregating many thresholded tests, so multiplicity control is not optional. The lack of such control undermines the reliability of the main prevalence conclusion.\n```r\n# Create a binary variable indicating whether Pvalue < 0.05\nef.size$value_sig <- ifelse(ef.size$Pvalue < 0.05, 1, 0)\n```\nThe provided analysis code operationalizes “occurrence” as a raw P-value cutoff at 0.05, consistent with the manuscript text, and it does so without adjustment for the number of tests. This makes the prevalence of “environment-induced changes” sensitive to the sheer number of coefficients tested, rather than solely to reproducible biological signal. Because the code converts every tested coefficient into a binary “significant/not” indicator, the downstream generalized linear mixed model is effectively modeling a discovery process that is known to contain false positives at roughly the nominal rate under null effects. If thousands of tests are performed, the expected number of false positives can become large even with modest dependence among tests. The code also suggests that significance is assessed per-coefficient rather than via a hierarchical model that would partially pool estimates and reduce spurious extremes. This code-level evidence therefore supports the critique that the paper’s “common” claim may be an artifact of uncorrected multiplicity.\n“It is often the case that thousands of features in a genomewide data set are tested against some null hypothesis, where a number of features are expected to be significant.” [[2]](http://engr.case.edu/ray_soumya/mlrg/Storey03.pdf)\nThis sentence captures a key statistical reality in large-scale testing: with many tests, a nontrivial number of apparently “significant” findings will arise even in the absence of true effects. The paper under review uses a similarly large-scale testing and counting approach (across genotypes, treatments, generations, and traits) but does not describe an approach to calibrate the expected false discovery burden. Standard practice in high-dimensional inference is to control a relevant error rate (e.g., FDR) when interpreting counts of significant results as evidence of prevalence. Without such calibration, “significant” does not translate into “common” or “pervasive” in a statistically meaningful way. The quotation therefore directly supports the claim that nominal significance thresholds are insufficient for robust prevalence conclusions. This is not a minor reporting issue; it affects the manuscript’s central quantitative conclusion.\n\nReferences:\n[2] [Storey JD, Tibshirani R. Statistical significance for genomewide studies. *PNAS* (2003).](http://engr.case.edu/ray_soumya/mlrg/Storey03.pdf)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|69|GPT|3", "source": "prb", "split": "test", "paper_id": "prb69", "comment": "This paper’s conclusion that genotype susceptibility to environmental induction is predictable from transposon abundance is not well supported because the regression uses transposon copy-number data for only a subset of genotypes (effectively n≈6 after excluding Col-0) and does not account for population structure/relatedness, making the reported correlations unreliable and non-generalizable.\n\n“we regressed the occurrence frequency of genotypes against different explanatory variables (climate of origin, methylation levels, and transposon abundance) and found that the abundance of transposons in the Gypsy (r = -0.840) and MuDR (r = 0.815) superfamilies explained a significant proportion of the variation”\nThis sentence presents strong correlation-based predictability claims, but correlation coefficients can be unstable and misleading in very small samples. The manuscript text does not state the sample size used for the transposon regressions in this Results paragraph, which is crucial for interpreting r and P-values. Moreover, the analysis appears to test multiple predictors (climate variables, methylation contexts, multiple TE superfamilies), which increases the risk that some predictors appear “significant” by chance without appropriate multiplicity control. Even if one or two correlations survive nominal thresholds, they may reflect shared ancestry or geographic structure rather than a mechanistic TE effect. The paper interprets these correlations mechanistically (“susceptibility… can be predicted”), which is much stronger than the evidence supports. This undermines the strength and generality of one of the headline claims.\n“These data were available for seven genotypes, including Abd-0, Ang-0, Col-0, Dja-1, Sap-0, Tol-0, and Ws-2 (Supplementary Table 1). The transposon data of Col-0 were not included in the subsequent analysis…”\nThis methods statement implies that the TE-based predictability analysis is conducted on at most six genotypes once Col-0 is excluded. With n≈6, any fitted regression is severely underpowered, and effect estimates (including r) are highly sensitive to single data points. In such a setting, model diagnostics, robustness checks (e.g., leave-one-out sensitivity), and explicit reporting of uncertainty become essential, but the Results paragraph reports the correlations as substantive predictors. Small-sample correlations are also especially vulnerable to confounding by population structure and relatedness, which are known to be strong in global Arabidopsis panels. The limited genotype coverage also conflicts with the broad framing that susceptibility is a general property “of a genotype” across the 14-genotype experiment. This is therefore a major limitation on the validity of the predictability claim.\n“A potentially serious obstacle to association mapping is confounding by population structure. It is well known that population structure may cause spurious correlations, leading to an elevated false-positive rate” [[3]](https://pmc.ncbi.nlm.nih.gov/articles/PMC1779303/)\nThis quotation states a general and well-established problem: correlations between genomic features and phenotypes can be spurious when individuals are related or structured. Although the paper under review is not doing GWAS, it is performing genotype-level regressions of “occurrence frequency” against genomic predictors (TE abundance), where population structure among accessions is a plausible confound. Because the manuscript does not model relatedness (e.g., via kinship/mixed models) in these regressions, it cannot distinguish TE-driven predictability from ancestry-driven correlation. This is especially concerning given the extremely small n implied by the TE-data availability. The external source underscores that “significant” correlations under structure should be treated cautiously and ideally supported by independent evidence. The manuscript does not provide such independent validation for the TE predictability.\n“However, genetic association studies in inbred model organisms are confronted by the problem of inflated false positive rates due to population structure and genetic relatedness among inbred strains…” [[4]](https://pmc.ncbi.nlm.nih.gov/articles/PMC2278096/)\nThis statement emphasizes that population structure and relatedness can inflate false positives even in inbred model-organism panels, directly relevant to Arabidopsis accessions. The manuscript’s TE predictability analysis uses simple regressions and reports nominal significance, but does not incorporate relatedness corrections that are standard when comparing genotype-level predictors across structured panels. Without such correction, the reported TE–susceptibility correlations can be artifacts of shared background rather than causal predictors. This limitation is amplified by the fact that TE copy number and many other genomic properties can covary with geography and demography. Therefore, even if the reported correlations are numerically large, they do not constitute reliable evidence of predictability. The quotation supports the critique that methodological safeguards against inflated false positives are necessary for the manuscript’s claim.\n\nReferences:\n[3] [Zhao K, Aranzana MJ, Kim S, et al. An *Arabidopsis* Example of Association Mapping in Structured Samples. *PLOS Genetics* (2007).](https://pmc.ncbi.nlm.nih.gov/articles/PMC1779303/)\n[4] [Kang HM, Zaitlen NA, Wade CM, et al. Efficient Control of Population Structure in Model Organism Association Mapping. *Genetics* (2008).](https://pmc.ncbi.nlm.nih.gov/articles/PMC2278096/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|69|GPT|4", "source": "prb", "split": "test", "paper_id": "prb69", "comment": "The paper’s transcriptomic conclusions about heritable DEGs and downstream enrichment/predictability are not reproducible as written because the manuscript specifies an adjusted-P and |log2FC| threshold that differs from the code’s actual filtering (raw p-values and a different fold-change cutoff), which can substantially change DEG sets and any claims derived from them.\n\n“the differentially expressed genes (DEGs) were filtered by | log2FoldChange | >1.5 and adjusted \\( P < 0.05 \\).”\nThis sentence specifies a stringent DEG definition using multiple-testing-adjusted P-values and a relatively high fold-change cutoff. Because the manuscript’s downstream results depend on the number of DEGs, the number of “heritable DEGs,” and overlap-based enrichment analyses, the exact DEG calling criterion is central to the validity of conclusions. If the analysis actually used raw P-values rather than adjusted P-values, the DEG list could contain many more false positives, especially across many genes and contrasts. Likewise, changing the fold-change threshold from 1.5 to 1 would materially increase the number of called DEGs and could inflate the number of genes appearing “heritable” across generations by chance. The paper does not provide sensitivity analyses showing robustness to these threshold choices. Therefore, inconsistency at this step compromises reproducibility of the gene-expression claims.\n```r\nfor (m in dds.name) {\n  dds.result <- results(dds2, name=m)\n  resOrdered <- dds.result[order(dds.result$pvalue),]\n  resSig <- subset(resOrdered,pvalue<0.05 & abs(log2FoldChange) > 1)\n  k=gsub('treat_','',m)\n  k=gsub('_vs_control','',k)\n  write.csv(as.data.frame(resOrdered),file=paste0(i,'/DEG/',i,'.',j,'.',k,'.all.csv'))\n  write.csv(as.data.frame(resSig),file=paste0(i,'/DEG/',i,'.',j,'.',k,'.remove.csv'))\n}\n```\nThe code applies a raw `pvalue < 0.05` threshold and `abs(log2FoldChange) > 1`, which directly contradicts the manuscript’s stated `adjusted P < 0.05` and `|log2FoldChange| > 1.5` criteria. This is not a cosmetic discrepancy: DEG lists can change dramatically when switching from adjusted to unadjusted P-values in RNA-seq, and those lists are then re-used to define “heritable DEGs” and to drive functional enrichment and TE analyses. Because the manuscript reports large ranges for numbers of DEGs and heritable DEGs (and interprets these counts biologically), readers must be able to reproduce exactly which genes were called. The mismatch also raises uncertainty about which pipeline generated the figures and extended-data results described in the manuscript. If the published results were produced with different thresholds than those described, then the reported statistics (e.g., counts and overlaps) are not verifiable from the provided code. This is a major reproducibility gap affecting key conclusions.\n“Rather, 0.013 is the expected proportion of false positives incurred if we call MSH2 significant.” [[2]](http://engr.case.edu/ray_soumya/mlrg/Storey03.pdf)\nThis sentence explains why using unadjusted thresholds in large-scale testing problems changes interpretation: calling items “significant” carries an expected false-positive burden that must be managed explicitly. In RNA-seq, where thousands of genes are tested per contrast, DEG calling conventionally relies on multiple-testing-adjusted measures specifically to control false discoveries. The manuscript claims to use adjusted P-values, which would align with this principle, but the code uses raw p-values, which does not. Because the paper’s “heritable DEG” definition requires significance in multiple generations, uncorrected p-values can still generate false persistence when the same genes are repeatedly tested. This makes any downstream biological interpretation of DEG sets and their enrichment sensitive to the mismatch. The quotation supports why the code–methods discrepancy is not just a documentation error but a validity risk.\n\nReferences:\n[2] [Storey JD, Tibshirani R. Statistical significance for genomewide studies. *PNAS* (2003).](http://engr.case.edu/ray_soumya/mlrg/Storey03.pdf)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|69|GPT|5", "source": "prb", "split": "test", "paper_id": "prb69", "comment": "The paper’s mechanistic inference that transposons are enriched around repeatedly induced (“susceptible”) genes is not robust because it relies on Col-0/TAIR10 reference gene and TE annotations despite known TE presence/absence variation across accessions, which can bias overlap/enrichment estimates when applied to non-reference genotypes.\n\n“we identified all heritable DEGs shared between genotypes or treatments (Extended Data Fig. 10a) and found that the abundance of members of several superfamilies, including Gypsy, HAT, Mariner, and Helitron, upstream and body of these susceptible genes was significantly higher than that of background genes (Extended Data Fig. 10b).”\nThis statement ties a central mechanistic claim (“nonrandom” genomic features) to an enrichment test that depends on accurate TE annotations and gene coordinates for the studied genotypes. However, the experiment uses multiple Arabidopsis accessions, and TE landscapes are known to vary substantially among accessions, so “upstream TE abundance” is genotype-dependent. If the enrichment is computed using a single reference annotation, it can misrepresent the true promoter and gene-body TE content in non-reference genomes. Because the paper interprets the enrichment as evidence that transposons mediate susceptibility, any systematic reference bias can create or erase apparent enrichment. The manuscript does not demonstrate that the same enrichment holds when using accession-specific TE calls or assemblies. Therefore, the mechanistic interpretation rests on an analysis that is potentially biased by construction.\n“We adopted the transposon annotation of TAIR10… Notably, our study adopted Col-0 as the reference, and genotype-specific genome assembly is necessary for a comprehensive understanding of this nonrandom phenomenon.”\nThis passage acknowledges that the analysis is performed in a reference coordinate system and that genotype-specific assemblies would be needed for a comprehensive interpretation. Given that the paper’s discussion elevates transposons to a “central role” and uses these enrichment results to motivate mechanistic explanations, this limitation is not peripheral—it directly affects the key mechanistic claim. If TE insertions/deletions or structural variants differ across accessions, overlap-based enrichment using a reference may systematically miscount TEs in promoters and gene bodies for many genotypes. The analysis therefore risks conflating reference-annotation completeness with biology, especially since the manuscript elsewhere notes that Col-0 has “biased (much more detailed) annotation of transposons.” Without repeating the enrichment with genotype-specific TE maps, the strength of the inference remains uncertain. This weakens confidence in the claimed genomic-feature nonrandomness.\n“Variation in the presence or absence of transposable elements (TEs) is a major source of genetic variation between individuals.” [[5]](https://elifesciences.org/articles/20777)\nThis quote establishes that TE presence/absence variation is pervasive and materially contributes to between-individual genomic differences in Arabidopsis. If TE content varies widely across accessions, then any enrichment analysis that uses a single reference TE annotation risks mischaracterizing TE neighborhoods for non-reference genotypes. The paper under review examines multiple accessions and uses TE-related features to explain susceptibility, so the existence of widespread TE PAV is directly relevant. A robust enrichment claim would ideally be evaluated using accession-specific TE calls (or at least sensitivity analyses) rather than relying on TAIR10 alone. The external evidence therefore supports why a reference-only TE enrichment test may not be sufficient. This is especially important when the enriched TE classes are used to motivate mechanistic pathways of induction.\n“It is challenging to identify the structural changes in the genome caused by TE mobilization using current short-read sequencing technologies as these reads are typically mapped to a reference genome, which has the effect of masking structural changes that may be present.” [[5]](https://elifesciences.org/articles/20777)\nThis sentence highlights a key technical limitation: mapping and annotation relative to a reference can mask structural variation such as TE insertions/deletions. The paper’s enrichment analysis is performed relative to TAIR10/Col-0 and then interpreted as reflecting genomic features of “susceptible” genes across genotypes. If structural differences are masked, then the computed TE overlaps around genes can be systematically biased toward the reference genome’s TE landscape. This bias is not merely theoretical; it is a known limitation in TE-variant discovery and interpretation in Arabidopsis populations. Because the manuscript’s central mechanistic conclusion depends on TE abundance estimates, the analysis needs to explicitly address this limitation empirically. The quoted literature supports that reference-based approaches can miss exactly the kinds of TE differences the manuscript invokes.\n“we found that, at heterozygous SNPs, there was a significant bias toward higher mapping rates of the allele in the reference sequence, compared with the alternative allele.” [[6]](https://pmc.ncbi.nlm.nih.gov/articles/PMC2788925/)\nAlthough this quote concerns SNPs and allele-specific mapping, the broader point is that reference-based mapping can introduce systematic bias that favors the reference sequence. In the present manuscript, both gene expression quantification and TE overlap analyses rely on mapping reads and features to a single reference genome (TAIR10/Col-0). Sequence divergence and structural differences among accessions can therefore alter mapping rates and apparent signal, potentially affecting which genes are called differentially expressed and which regions appear TE-rich. This is relevant because the enrichment test is performed on the set of “heritable DEGs,” which itself depends on mapping and DEG calling. If reference bias influences DEG selection, it can indirectly influence TE enrichment as well. The external evidence supports why reference-based analyses across divergent genotypes require careful bias mitigation and validation.\n\nReferences:\n[5] [Stuart T, Eichten SR, Cahn J, et al. Population scale mapping of transposable element diversity reveals links to gene regulation and epigenomic variation. *eLife* (2016).](https://elifesciences.org/articles/20777)\n[6] [Degner JF, Marioni JC, Pai AA, et al. Effect of read-mapping biases on detecting allele-specific expression from RNA-sequencing data. *Bioinformatics* (2009).](https://pmc.ncbi.nlm.nih.gov/articles/PMC2788925/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|69|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb69", "comment": "The paper fails to correct for multiple comparisons in the analysis of phenotypic changes, leading to a high likelihood of false positives and inflating the perceived prevalence of \"heritable\" variations.\n\n```r\n# Create a binary variable indicating whether Pvalue < 0.05\nef.size$value_sig <- ifelse(ef.size$Pvalue < 0.05, 1, 0)\n```\nThis code snippet from `glm.R` demonstrates that the authors define a significant effect based on a raw P-value threshold of 0.05. Given that the study involves 14 genotypes, 10 treatments, 4 generations, and 5 traits (totaling thousands of statistical tests), using an uncorrected P-value will result in a large number of false positives by chance alone. Standard statistical practice requires correcting for the False Discovery Rate (FDR) using methods like Benjamini-Hochberg [1] when performing such a large number of simultaneous tests.\n```r\nCalculate_ef_size <- function(matr, treat_list, gen_list, trait_list) {\n    result_list <- lapply(trait_list, function(trait) {\n      trait_results <- lapply(treat_list, function(treat) {\n        # ... (looping through treatments)\n            result <- lapply(gen_list, function(gen) {\n              # ... (looping through generations)\n              mod <- lmer(formu, na.action = na.omit, data = matr.sub[matr.sub$Generation == gen, ])\n              coef_summary <- coef(summary(mod))\n              data.frame(treat = treat, gen = gen, trait = trait, coef_summary)\n            })\n        # ...\n      })\n    # ...\n    })\n    # ...\n}\n```\nThis code from `Effect_size.R` shows that the authors fit separate linear mixed models for each combination of trait, treatment, and generation, and extract the raw P-values (`coef(summary(mod))`) without any adjustment for the multiplicity of testing. The subsequent analysis of \"occurrence frequency\" and \"susceptibility\" relies entirely on these uncorrected P-values, rendering the conclusions about the prevalence and predictability of heritable changes statistically invalid.\n\"The statistics showed that the genotype, environmental treatment and their interaction significantly affected all phenotypes measured (except for the interaction effect on flowering time, Supplementary Table 2).\"\nThis statement in the Results section implies robust statistical significance, but the underlying methodology reveals that these \"significant\" effects are likely inflated by the lack of multiple testing correction. Without proper FDR control, it is impossible to distinguish true biological signals from stochastic noise, undermining the central claim that environment-induced heritable variations are \"common\".\n\nReferences:\n[1] Benjamini, Y., & Hochberg, Y. (1995). Controlling the false discovery rate: a practical and powerful approach to multiple testing. Journal of the Royal statistical society: series B (Methodological), 57(1), 289-300.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|69|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb69", "comment": "The code used for differential expression analysis contradicts the Methods section and uses invalid statistical criteria (unadjusted P-values), rendering the gene expression results and subsequent transposon enrichment analysis unreliable.\n\n```r\nresSig <- subset(resOrdered,pvalue<0.05 & abs(log2FoldChange) > 1)\n```\nThis line from `transcriptom analysis.R` shows that the authors filter differentially expressed genes (DEGs) using a raw `pvalue < 0.05` and a log2 fold change greater than 1. In RNA-seq analysis, it is standard practice to use adjusted P-values (FDR) to control for the thousands of gene tests performed [2]. Using unadjusted P-values will yield a massive number of false positive DEGs, which invalidates the claim that \"heritable gene expression changes were common\".\n\"The expression matrix was normalized by function vst in package “DESeq2”. The difference in gene expression was estimated with function DESeq, and the differentially expressed genes (DEGs) were filtered by | log2FoldChange | >1.5 and adjusted \\( P < 0.05 \\).\"\nThis sentence from the Methods section explicitly claims that an adjusted P-value threshold and a stricter fold change cutoff (>1.5, approx. 2.8-fold) were used. The discrepancy between the described methodology and the actual code (unadjusted P < 0.05, >2-fold change) is a serious issue that misrepresents the rigor of the analysis and casts doubt on the validity of all downstream analyses, including the functional enrichment and transposon correlation results.\n\nReferences:\n[2] Love, M. I., Huber, W., & Anders, S. (2014). Moderated estimation of fold change and dispersion for RNA-seq data with DESeq2. Genome biology, 15(12), 550. https://doi.org/10.1186/s13059-014-0550-8", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|69|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb69", "comment": "The definition of \"heritable\" as changes occurring in at least two out of four generations is insufficiently rigorous and likely captures stochastic variation rather than stable inheritance.\n\n\"Importantly, a substantial proportion (36.8% 10.4%, and 7.5%) of these changes occurred in two, three, and four offspring generations, suggesting that these environment-induced changes were heritable.\"\nThe authors classify any change that is significant in at least two generations as \"heritable\". However, true transgenerational inheritance typically implies stable transmission across generations or a consistent decay. A change that appears in F1, disappears in F2, and reappears in F3 (which would count as \"heritable\" under their definition) is more likely due to experimental noise or stochastic plasticity than stable epigenetic inheritance. Only 7.5% of changes persisted across all four generations, suggesting that stable inheritance is actually rare, contradicting the paper's title and main conclusion.\n\"In summary, parental environmental effects are common and often strong in A. thaliana, but they are genotype-dependent and difficult to predict.\" [3]\nPrevious work by Latzel et al. (2023) found that while parental effects are common, they are unpredictable and often unstable. The current paper's loose definition of heritability inflates the apparent stability of these effects, potentially masking the stochastic nature of the phenomenon observed in other studies.\n\nReferences:\n[3] Latzel, V., Fischer, M., Groot, M. P., Giseke, D., & van Kleunen, M. (2023). Parental environmental effects are common and strong, but unpredictable, in Arabidopsis thaliana. New Phytologist, 237(3), 1014-1023. https://doi.org/10.1111/nph.18573", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|69|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb69", "comment": "The failure of the controlled experiment (Test II) to improve the reproducibility of effect sizes compared to the heterogeneous experiment (Test I) suggests that the observed variations are likely due to stochastic noise or experimental error rather than robust biological effects.\n\n\"Surprisingly, the repeatability of the effect sizes between generations in Test II did not increase compared to that in Test I (Fig. 3d, Extended Data Fig. 4a).\"\nThe authors designed Test II specifically to eliminate environmental heterogeneity between generations, which they hypothesized was the cause of variation in Test I. The fact that reproducibility did not improve implies that the variation is intrinsic or due to measurement error, rather than environmental noise. This finding undermines the claim that these are robust, biologically meaningful heritable changes, and instead points towards stochasticity or experimental artifacts.\n\"The plot showed considerable variation in the magnitude and direction of the phenotypic changes.\"\nThe observation that phenotypic changes vary in both magnitude and direction across generations and genotypes further supports the idea that these are not stable, adaptive responses. If the direction of the effect flips between generations (e.g., larger plants in F1, smaller in F2), it is difficult to argue for a consistent heritable mechanism or adaptive value.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|69|Gemini|5", "source": "prb", "split": "test", "paper_id": "prb69", "comment": "The correlation between transposon abundance and \"susceptibility\" is based on a small sample size and potentially spurious metrics derived from uncorrected P-values, and lacks direct mechanistic evidence.\n\n\"Intriguingly, the susceptibility of a genotype to environmental inductions could be predicted based on the transposon abundance in the genome.\"\nThis correlation is based on a sample size of only 14 genotypes (or 10 in Test II). With such a small sample size and high-dimensional genomic data (multiple transposon superfamilies), high correlations can easily arise by chance or be driven by outliers. Furthermore, the \"susceptibility\" metric itself is derived from the \"occurrence frequency\" of significant changes, which, as noted in Item 1, is flawed due to the lack of multiple testing correction. If the \"susceptibility\" scores are largely noise, any correlation with genomic features is likely spurious.\n\"Our study... suggest that the environment can broadly contribute to the generation of heritable variation... transposons play a central role\".\nThe paper claims a central mechanistic role for transposons but provides only correlational evidence based on baseline transposon abundance. There is no direct evidence presented (e.g., bisulfite sequencing of treated lines, transposon mobilization assays) to show that transposons are actually moving or changing their methylation state in response to the environmental treatments in the offspring generations. Without such mechanistic validation, the link remains speculative.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|69|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb69", "comment": "“..The frequency of occurrence of fruit number was…” – delete “number”; is it actually just seed amount? “the frequency of occurrence of fruit” sounds weird – sounds like some plants had no fruits.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|69|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb69", "comment": "“the number of genes showing heritable expression changes can be predicted by the abundance of transposons in the genomes.” – I would use the word “correlate”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|69|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb69", "comment": "Please elaborate on pooling F1 – F4 seeds together for the Test II. Seeds from how many plants were pooled? By weight or by number?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Claude|1", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "The paper draws strong conclusions about the relative importance of different factors (social learning, maternal effects, environmental similarity, heritability) in explaining dietary specialization, but the reported credible intervals for several variance components are extremely wide, spanning from near-zero to substantial values, which undermines the certainty of these conclusions.\n\n\"Genetically more closely related individuals did not share a more similar trophic position (3% [< 0.1% – 17%] of variance explained) providing no evidence that dietary specialization could be heritable in this population\"\nThe credible interval for heritability spans from less than 0.1% to 17%, which is a range from effectively zero to a biologically meaningful contribution. A 17% contribution would actually be considered substantial in quantitative genetics studies of wild populations. The authors' conclusion that heritability is \"negligible\" is not fully supported when the upper bound of the credible interval includes values that would typically be considered meaningful. According to Postma (2014), the median heritability estimate from animal models in wild populations for life history traits is around 0.26, meaning 17% would be within the typical range observed in the field. The width of this interval suggests insufficient statistical power to reliably distinguish between negligible and moderate heritability.\n\"Additionally, maternal effects accounted for 11% [0.5% − 30%] of variation in trophic position\"\nThe credible interval for maternal effects ranges from 0.5% to 30%, indicating high uncertainty in this estimate. The six-fold difference between the lower and upper bounds makes it difficult to confidently conclude that maternal effects explain more variance than other factors. This wide interval suggests that with the available sample size and pedigree structure, the data cannot precisely distinguish between minimal and substantial maternal effects. According to de Villemereuil et al. (2013), such imprecision is common when sample sizes are limited for variance partitioning in animal models.\n\"A remaining 8% [0.3–26%] of variance in trophic position was attributed to permanent individual effects\"\nSimilar to other variance components, the permanent individual effects have a credible interval spanning from 0.3% to 26%, an 87-fold range between lower and upper bounds. This level of uncertainty makes comparisons between variance components unreliable. For instance, the paper cannot statistically distinguish whether permanent individual effects contribute 8% (less than maternal effects at 11%) or 26% (substantially more than maternal effects). This undermines the paper's ranking of factor importance.\n\"Our simulations showed that the animal model was the best approach to estimate heritability, using REML for Gaussian phenotypic traits and MCMC for binary traits. We join previous authors (Quinn et al. 2006; Postma & Charmantier 2007) in pointing out the importance of data quantity and quality: our simulations revealed the high level of imprecision for estimates given by some approaches and estimation methods for a sample size of 200 individuals, which may be considered already a large sample in studies on wild populations.\" [[1]](#citation-1)\nThis quote from a methodological study on heritability estimation highlights that even 200 individuals may produce imprecise estimates. The current study has 213 hair samples from 71 females with 33 mothers, which is a complex but relatively modest sample for partitioning variance across multiple components (environment, genetics, maternal effects, maternal learning, and individual effects). The literature suggests that precision in variance component estimation requires substantial sample sizes and well-connected pedigrees, conditions that may not be fully met here.\n\nReferences:\n[1] de Villemereuil, P., Gimenez, O., & Doligez, B. (2013). Comparing parent–offspring regression with frequentist and Bayesian animal models to estimate heritability in wild populations: A simulation study for Gaussian and binary traits. Methods in Ecology and Evolution, 4(3), 260-275. https://besjournals.onlinelibrary.wiley.com/doi/10.1111/2041-210x.12011", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Claude|2", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "The paper interprets the correlation between maternal trophic position and offspring trophic position as evidence for \"social learning\" or \"maternal learning,\" but this correlation could arise from multiple mechanisms beyond direct observational learning during rearing, and the statistical approach cannot distinguish among these alternative explanations.\n\n\"Similarities between the dietary phenotypes of mothers and their offspring indicate social learning of resource preference or competence to secure a resource by the offspring from the mother during early ontogeny\"\nThis statement assumes that mother-offspring similarity in trophic position is attributable to social learning, but the correlation could also result from: (1) shared microhabitat exposure during the rearing period that independently affects both mother and offspring diets, (2) physiological imprinting through maternal milk composition during nursing, (3) genetic effects not fully captured by the pedigree-based heritability estimate, or (4) shared responses to environmental conditions within overlapping home ranges after separation. Social learning, as defined in the animal behavior literature, requires specific criteria including the acquisition of behavioral patterns through observation or interaction, which was not directly observed or tested in this study.\n\"In this review, we will explore current knowledge on the contexts in which social learning occurs in non-human animals and the brain mechanisms underlying such forms of learning. Social learning can happen through a variety of mechanisms that may include effects of others on attention, learning stimulus or action value through observation, motor simulation and imitation and active instruction using movements or sounds.\" [[2]](#citation-2)\nThis definition from a review on social learning mechanisms emphasizes that social learning involves specific cognitive and behavioral processes such as attention effects, observational value learning, motor simulation, imitation, and instruction. The current study does not provide evidence for any of these specific mechanisms; it only demonstrates a statistical correlation that decays over time. The correlation is consistent with social learning but is equally consistent with other non-learning mechanisms that could produce mother-offspring similarity in diet.\n\"Social learning is defined in terms of its outcome rather than its underlying process. It can thus result from varied processes and mechanisms\" [[3]](#citation-3)\nWhile social learning is indeed sometimes defined by outcomes, attributing the observed correlation specifically to \"learning\" implies an active cognitive process of behavioral acquisition. The statistical approach used cannot distinguish between true learning (where offspring acquire dietary preferences through observation) and other mechanisms such as shared environmental exposure or physiological effects. Without behavioral observations or experimental manipulations, the term \"learning\" may overstate what the statistical correlation demonstrates.\n\"We interpret this relationship as evidence that maternal learning plays an important role in shaping an individual's dietary specialization. Five years into independence, the similarity between the mothers' and their daughters' trophic position slowly faded, likely due to individual learning and experience.\"\nThe temporal decay of mother-offspring similarity is presented as evidence consistent with social learning (initial learning followed by individual modification). However, this pattern could equally arise from initially overlapping home ranges that gradually diverge as daughters establish their own territories, or from initially similar environmental conditions that change over time. The interpretation of the decay pattern as \"individual learning and experience\" replacing \"maternal learning\" assumes the initial correlation was due to learning, which is not empirically established.\n\nReferences:\n[2] Joëlle, C. S., & Apps, M. A. J. (2014). Social learning in humans and other animals. Frontiers in Neuroscience, 8, 58. https://www.frontiersin.org/articles/10.3389/fnins.2014.00058/full\n[3] Heyes, C. (2016). Animal social learning: associations and adaptations. F1000Research, 5, 2120. https://pmc.ncbi.nlm.nih.gov/articles/PMC5007745/", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Claude|3", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "In this female philopatric species where daughters settle near their mothers, spatial proximity inherently confounds maternal effects, environmental effects, and the proposed social learning effect. While the paper acknowledges this confounding, the analytical approaches used cannot fully disentangle these effects, limiting causal interpretation.\n\n\"Specifically, in female-biased philopatric species, spatial proximity does not only encode for spatial variation in resource abundance but is also conflated with relatedness and, in particular, with maternal effects.\"\nThe paper acknowledges this fundamental confounding issue but proceeds to draw conclusions about the relative importance of different factors. In philopatric species, daughters settling near mothers creates an inherent correlation structure where: (1) daughter and mother share similar environments, (2) daughter and mother have genetic similarity, (3) daughters of the same mother share similar environments and genetics with each other, and (4) any \"learned\" behaviors during rearing could also be explained by shared early-life environment. The animal model attempts to partition these effects, but when they are structurally correlated, statistical separation becomes unreliable.\n\"After excluding spatial distance, maternal learning and maternal effects but not heritability explained more variance in trophic position, corroborating that spatial proximity is confounded with philopatric females forming clusters of mothers and daughter in space, so called matrilines\"\nThis supplementary analysis demonstrates that model specification (including vs. excluding spatial distance) substantially changes the variance attributed to different components. The fact that excluding spatial distance increases the variance attributed to maternal learning and maternal effects indicates that these effects are partially confounded with spatial proximity. This makes it difficult to confidently determine how much of the observed mother-offspring similarity is due to actual learning versus shared spatial environment.\n\"spatial proximity explaining 59% of the total phenotypic variation in trophic position of female bears: individuals further apart tended to have more different diets. However, when replacing spatial proximity with environmental similarity among home ranges, the explanatory power was attributed to maternal learning and maternal effects along with the environment.\"\nThis finding reveals a crucial methodological issue: when spatial proximity is included, it explains 59% of variance; when it is replaced with environmental similarity, variance is redistributed to maternal learning and maternal effects. This redistribution reflects the statistical substitutability of these correlated predictors rather than a biological distinction. The choice of which variable to include (spatial distance vs. environmental similarity) fundamentally affects the conclusions about which factors drive dietary specialization, yet this choice is somewhat arbitrary when these variables are highly correlated.\n\"For example, given two pedigrees with identical sample sizes, a pedigree with a weak degree of connectivity between individuals, for example, in populations with strong natal dispersion and/or immigration resulting in few related individuals, will be less precise than a pedigree with known relationships between all individuals\" [[4]](#citation-4)\nThis quote from a study on quantitative genetics highlights how pedigree structure affects the reliability of variance component estimates. In the current study, the philopatric structure where daughters settle near mothers creates high correlation between spatial, genetic, and maternal variables, which reduces the ability of the animal model to reliably partition variance among these sources. The precision of estimates depends not just on sample size but on the independence structure of the data.\n\nReferences:\n[4] de Villemereuil, P., et al. (2016). An assessment of the reliability of quantitative genetics estimates in study systems with high rate of extra-pair reproduction and low recruitment. Heredity, 118, 229-238. https://www.nature.com/articles/hdy201692", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Claude|4", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "The primary analysis uses model-averaged maternal trophic positions rather than directly observed values during the rearing period, and the supplementary analysis with observed values shows nearly double the variance explained by maternal learning (22% vs 13%), raising questions about the accuracy of the main results.\n\n\"Our estimates of maternal learning are therefore likely conservative and may underestimate the true effect of maternal learning on dietary specialization.\"\nThe authors acknowledge that their main estimate may be conservative, but this acknowledgment appears in the discussion rather than prominently in the abstract or main conclusions. The 13% figure for maternal learning is featured in the abstract and throughout the paper, while the potentially more accurate 22% estimate from the sensitivity analysis receives less attention. If the true effect of maternal learning is closer to 22%, this would change the interpretation of the relative importance of different factors.\n\"maternal learning explained even more of the phenotypic variance in daughter trophic position (22% [8% − 27%] instead of 13%, Supplementary material S10) when fitting the observed maternal trophic position during rearing, instead of the modelled posterior average maternal trophic position to a reduced dataset (62 hair samples collected from 38 daughters)\"\nThe difference between 13% and 22% variance explained is substantial—nearly a 70% increase. This suggests that the method of measuring maternal trophic position significantly affects the conclusions. The fact that using observed values during rearing produces a larger effect raises the question of whether the modeled values introduce measurement error that attenuates the estimated relationship. However, the reduced sample size (62 vs 213 samples) in the sensitivity analysis also introduces uncertainty about which estimate is more reliable.\n\"While the modelled maternal trophic position correlated strongly with the observed trophic position in any given year (Supplementary material S3)\"\nThe authors note strong correlation between modeled and observed values, but correlation does not preclude measurement error that could attenuate regression coefficients. If the modeled maternal trophic position contains measurement error (variance not related to the true maternal trophic position during rearing), classical errors-in-variables theory predicts that this would bias the estimated effect toward zero. The substantial difference in results between the main and sensitivity analyses suggests this may be occurring.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Claude|5", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "There is an apparent discrepancy in the reported variance explained by environmental similarity between different sections of the manuscript, which affects the reproducibility and clarity of the results.\n\n* Quote (Abstract): \"The main determinants of this dietary specialization were maternal learning during rearing (13%), environmental similarity (12%), maternal effects (11%), and permanent individual effects (8%)\"\nThe abstract reports environmental similarity as explaining 12% of variance in trophic position. This is one of the headline findings presented to readers.\n\n* Quote (Results): \"environmental similarity accounted for 9% [0.1–5%] of the total phenotypic variation in trophic position\"\nThe Results section reports environmental similarity as explaining 9% of variance, with a credible interval of [0.1-5%]. There are two issues here: first, the 9% in Results differs from the 12% in the Abstract; second, the credible interval [0.1-5%] appears to be incorrectly reported because the median (9%) should fall within the credible interval. A median of 9% cannot have a credible interval of [0.1-5%] because 9 is outside this range. This appears to be either a transcription error or a reporting mistake that should be clarified, as it affects readers' ability to evaluate the precision of the environmental similarity estimate.\n\n* Quote (from published version in Nature Communications): \"environmental similarity (5%)\"\nThe published version of this paper in Nature Communications reports environmental similarity as 5%, which differs from both the 12% in the preprint's abstract and the 9% in the preprint's results section. While the preprint being reviewed may represent an earlier version, the discrepancies between reported values suggest either calculation changes during revision or reporting inconsistencies that should be reconciled for clarity. These differences affect the interpretation of the relative importance of environmental versus social factors.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Abstract] L37: The apostrophe after “species” is not really necessary.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Abstract] L39: Add a comma after “drivers”. Use the plural of remain (remains).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Abstract] L42: After reading the manuscript, I’m not entirely clear on what you mean by “environmental forcings”. As you only use this term in the abstract (here and L50), I suggest using more relevant terminology that matches the main text.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Abstract] L46-47: Rephrase: “the trophic position of offspring closely”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Abstract] L49: Replace “reveals” with “shows”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] My primary concern with the introduction is how maternal learning is differentiated from maternal effects, offspring learning, environmental effects and genetic effects. It seems to be blended together, and the definitions do not provide much clarity. I suggest using “offspring learning” rather than “maternal learning” if this is what you really mean (as suggested on L114). But this needs to be clearly differentiated from maternal dietary effects (e.g. offspring gaining information about food resources during suckling).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L61: Replace “hence” with “likely”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L62: Add a comma after “composition”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|9", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L63: Rephrase: “key for driving species resilience in response to”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|10", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L64: A comma may be useful after “world”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|11", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L66 onwards: This paragraph was very long and incorporated many different ideas. The concept of environmental effects wasn’t well developed in contrast to the other ideas. The issue with separating out maternal learning and maternal effects is that mothers can still affect offspring postnatally because of the environment they might be experiencing independently of their offspring. I suggest breaking this paragraph up and systematically discussing each topic clearly and unambiguously.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|12", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L66: The comma after “opportunity” is not necessary.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|13", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L68: Replace “yet” with “however”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|14", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L69: Bring “been” after “rarely”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|15", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L71: This should simply be parental effects. Fathers can also affect offspring development and behaviour even in species without paternal care. I suggest introducing the concept broadly, and then discussing maternal effects specifically within that context.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|16", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L74: Rephrase: “between the dietary phenotypes of mothers and their offspring”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|17", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L75: Replace “are” with “may be”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|18", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L78-79: Again, paternal effects may also be important. As suggested, restructuring this paragraph and then focusing on parental effects specifically will allow you to introduce the concept broadly and then refine it to explain why maternal effects are a potentially stronger factor for solitary species.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|19", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L81: Please provide a reference for this statement. It is not clear why maternal effects would be evident from the similarity of repeated samples of siblings. Couldn’t a genetic effect equally result in a similar response between siblings?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|20", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L82-83: Likewise, please provide a reference for this statement. It is not clear why similarity between mothers and offspring reflects maternal learning (which should be defined here because it’s not clear) when similarity could be a consequence of genetic effects, maternal effects or offspring learning from their mothers.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|21", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L94: Add a comma before “we then attributed”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|22", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L99: I suggest “newborn ungulates” rather than “ungulates neonates”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|23", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L100: Hyphenate “plant-based”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|24", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L101: Delete the comma before “however” and replace with a semi-colon.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|25", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L106: Use plural “sources”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|26", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L107: I suggest starting a new paragraph before “Brown bears”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|27", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L110: Add a comma after “mother”. Replace “assume” with “predict”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|28", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L112: Add “may” after “hence”. Use plural “behaviors”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|29", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L113: Delete “hence”. Replace “of” with “from”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|30", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L114: Delete the comma before “however” and replace with a semi-colon.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|31", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L116: But body size is also strongly influenced by environmental effects, such as resource availability, so could equally affect maternal effects through effects on maternal environment.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|32", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L117: Add a comma after “population”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|33", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L121: With reference to “leading to greater similarity” - This assumes no competition between siblings (either in utero or ex utero). Runts could be argued to gain fewer maternal resources, so why would you expect similar trophic positions if there are differences?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|34", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L123: I suggest starting a new paragraph before “To assess”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|35", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L128: Delete the comma after “may”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|36", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L132: Past tense: “fitted”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|37", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L133: Consider “untangle” rather than “disentangle”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|38", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L134: Delete “as determinants of” and replace with “to”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|39", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L136: Add a comma after “ranges”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|40", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L137 and elsewhere: I suggest putting all the “such as” parts in brackets as examples. “Mature habitat (e.g. old and mid-successional forests)” – and so on.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|41", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L142: Should this read: “a mother’s trophic position on her daughters’ trophic positions”?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|42", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L144: Why does 3 come first? Consider reordering to have the material presented in numerical order.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|43", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L146: Replace “last” with “Finally”:", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|44", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L150: Why is this in supplementary material only and not in the main text? Perhaps indicate here why you provide this information as supplementary, considering you make the point that you are focusing on daughters.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|45", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L156: Delete “last”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|46", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Results] L162 Replace “in” with “from”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|47", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Results] L164: Replace “revealed” with “showed”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|48", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Results] L177: Delete “as”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|49", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Results] L179: But in L176 you say that siblings were more similar in trophic position. So how do you know this is a maternal effect and not a genetic effect? Please elaborate.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|50", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Results] L183: Replace “as” with “to”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|51", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Results] L193: Start the point after the colon with a small letter “a”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|52", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Results] L194: Commas before and after “but not heritability” could increase the clarity and flow of this sentence.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|53", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Results] L195-196: Perhaps I missed something here, but I don’t understand how controlling for spatial proximity showed that it was a confounding effect. Perhaps consider additional elaboration for clarity here.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|54", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Results] L201: Rephrase: “offspring trophic position”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|55", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Discussion] L246: Rephrase: “between the trophic position of mothers and daughters slowly”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|56", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Discussion] L251: Delete the comma before “however” and replace with a semi-colon, adding a comma after “however”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|57", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Discussion] L253: Using the term “early-life imitation” here is confusing. As suggested earlier, I suggest using a single term, offspring learning, in place of others (including maternal learning) so that the reader isn’t left confused in the discussion.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|58", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Discussion] L258: Replace “adapt” with “respond flexibly” as this is likely a better reflection of what is occurring, rather than adapting (in the classic evolutionary sense).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|59", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Discussion] L275: Delete the comma after “parental care”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|60", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Discussion] L278: Singular “remain”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|62", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Discussion] L293: Rephrase: “over their lifetimes, further indicating the crucial”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|63", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Discussion] L295: Add a comma after “resources”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|64", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Discussion] L297: Delete the comma after “effects”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|65", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Discussion] L300: Delete the comma after “specialization”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|66", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Discussion] L306: Consider “untangle” rather than “disentangle”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|67", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Methods] L369: Rephrase: “diet of brown bears in”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|68", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Methods] L379: Please indicate what times seed preference tests were conducted.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|69", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Methods] L391: Delete “that”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|70", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Methods] L423: Consider “Furthermore” rather than “further”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|71", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Methods] L461: Delete the comma after “deviation” and replace with a semi-colon.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|72", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Methods] L473: Past tense “fitted”.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_1|73", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Supplementary Materials] It was disappointing that most of the supplementary material was not referred to in the main text to provide context. I suggest adding the citations to the supplementary material at relevant and appropriate points in the text so that the reader has context and can expand their understanding as necessary.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] I feel that the second paragraph needs to be rearranged to be clearer and more effective. It might not be easy to understand how the different mechanisms differ from each other. For example, it says maternal learning and maternal effect, but in my opinion maternal learning is part of maternal effect (and it is more or less what you say in the supplementary “maternal effects (both maternal learning and maternal effects)”). Regarding maternal learning mechanisms, I am confused by the use of interchangeable words between maternal imitation and learning. Imitation is a special case of learning, but it would be better to stick to one term. Regarding genetic inheritance mechanisms, I think that maternal genetic effect is a kind of (indirect) genetic inheritance.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L58 add (a.k.a. individual specialization) or L60 add individual specialization (i.e. among-individual variation of niche).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L63 Are you talking about among or within individual variation?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L63-65 I think the flow in the first paragraph will be better if this sentence is moved right after the first one (L59).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L66-68 Does this apply to all types of individual specialization or just individual dietary specialization?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L-68- among-individual variation or both among and within?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L-70 Four non-exclusive potential sources. Do you have any references to justify these four potential sources?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L70-73 What I think is not clear here is that part of the maternal effect can be social learning and part of the maternal effect can also be (indirect) genetic inheritance.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|10", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L82-83 (e.g. maternal learning). Maternal learning might be one of the reasons of similarity between offspring and mothers.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|11", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L88-90 Multigenerational pedigree is not required if you do an experimental approach, so I would specify that this approach is required in wild populations.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|12", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L113 Why imitation and not direct learning? and how maternal learning differs from maternal effect?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|13", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L118 Maternal effects (i.e. maternal genotype or maternal environment) should come when you first mention maternal effects.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|14", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Introduction] L120-121 I don’t think that genetic and environmental differences are two exclusive explanations.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|15", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Results] I agree that the maternal learning effect can fade over time, but so can the other maternal effects, such as the genetic and environmental maternal effects. Can you explain why you made the choice to account for time since separation for maternal learning but not for the other maternal effects (random effect part)? Ignoring time for the maternal effect could, in part, bias your estimate of heritability downward. In addition, given that you have motherID and pedigree, I was wondering if there was any particular reason not to partition the maternal effect variance into genetic and environmental maternal effect.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|16", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Results] I did not understand why the time x maternal trophic position was considered as maternal learning? You show in L119-137 of the supplementary material that the distance between offspring and mother increases with time. So your interaction time by maternal position effect might just be a spatial effect due to dispersal and not due to learning fading over time.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|17", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Results] L162- You said 72 females in the introduction.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|18", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Results] L226-229 The legend labels need to be more precise: environment -> environmental similarity to be consistent with the text legend; permanent individual -> permanent environment (to be more consistent with quantitative genetic litterature?).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|19", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Results] Heritability is a ratio and not the variance components of interest, so something like \"direct additive genetic\" would be better. Please make sure this figure is color blind friendly (same for figure 3).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|20", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Discussion] The authors mainly discuss the results of maternal learning, which gives the feeling that they only studied this effect, which is not the case. There are other components that are interesting and have been poorly studied in the literature.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|21", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Discussion] L257 The 8% permanent effect can also be due to a cohort effect and many other things.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|22", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Discussion] L262 Sometimes you have distinguished social and maternal learning, sometimes you have used them as synonyms.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|23", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Discussion] L289- But if there is social learning, do you think that removing one problematic individual from the population will be enough?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|24", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Methods] I think this section also needs more guidance for the reader. First, it is not clear on what number of individuals you did the quantitative genetic analysis. Then I think it would be nice to have the model equation to better understand all the effects that were tested. You have a lot of different variance components and it is not clear what all your components together represent. For example: permanent environment is between individual differences not explained by additive genetic, maternal effect, habitat similarity, etc. For the maternal learning vs. maternal effect variance components, you could perhaps specify that maternal effect it is the rest of the maternal effect that is not learning. Finally, it might be good to specify what percentage of females disperse and at what distance, so that we can better understand the biological conditions under which we can disentangle environmental similarity from other components.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|25", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Methods] L399- Please provide quick pedigree summary statistics (such as the number of generations).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|26", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Methods] L433 It would be good to know the average home range size of the bears so that we can find out that 25 m spatial resolution is good.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|27", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Methods] L458-459-472 You should add that you calculated the relative importance of each variance component and the associated credible interval, since these are the values you provided in the text. It might also be nice to provide the estimated variance of the full model in the supplementary materials.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|28", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Supplementary] L78-79 : Why is it written \"among individual variation explains all the variance in trophic position\" when the R^2 is 45% ?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|29", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Supplementary] L148-147 : I don't understand why the spatial distance approach is better for this particular point (since it gives no information about ant or moose density). Individuals close in space may have similar phenotypes, but you will not know if this is due to similar moose/ant densities.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|30", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Supplementary] L156-157 Similar trophic positions due to social learning or shared genes.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|31", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Supplementary] L170-171 It will be worthwhile to provide the autocorrelation coefficients by distance class so that we can understand at what spatial scale your habitat composition is autocorrelated and whether it's less than the dispersal distance.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_2|32", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Supplementary] L184 Why 98% and not 89% as in the main text?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "Lines 123-159 in the Introduction reads more like Methods than Introduction material. The authors even include references to Fig. 1A and Supplemental material before any results are included. I would suggest the authors include readily defined hypothesis, objectives, or predictions then use those for organizing the methods and results.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "The amount of details on stable nitrogen isotopes timing in hair (Lines 126-131) appears to be Methods that are placed into the objectives or it could be introductory material that might be better in a separate paragraph before your objectives. It appears that the majority of your analysis is based on accumulation of diet in hair so perhaps including these details in a separate paragraph, and adding more detail on how it has been done in bear or other species, would set up your final paragraph better than how it is currently constructed using Fig. 1?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "Based on 1 above, it is not clear in the Methods, which of these methods were needed for each objective because each objective is loosely presented.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "Related to 3 above, if hair is from “known” mother-daughter pairs (Line 132), and the methods in the Pedigree section were from Frank et al., then there is no need to include this in your methods. I would suggest you state that mother-daughter pairs were determined in Frank et al. and not include the paragraph Genetic Pedigree and parentage assignment in the Methods because that component was already completed prior to this effort.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "Fig. 1A: It is not clear to me the need or intent for this figure? It seems citations confirming the relationship of diet to hair and hair growth across bear and different species as suggested above would be more valuable than a figure of this nature. In addition, the text cites Jimbo et al. and Cattet et al. for Fig. 1A so was this created and presented in those publications? If so, it should not be included here. If it was created in this effort then it should be in Methods and a Result of this work and not in the Introduction.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Methods] Lines 367-370: The paragraph states that natural foods, plural, were collected but only moose hair was collected. Why was only moose hair and not muscle collected considering bear likely are not eating a great deal of hair? Would the authors expect moose hair and muscle to be similar in nitrogen stable isotopes or were both measured to confirm? It is not clear to me that hair is a good measure or comparable measure of muscle or reflective of stable nitrogen isotopes that would be incorporated into bear hair.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_3|7", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Methods] It appears that other food items were collected (Supplemental Figure S1) but only moose were referenced here in the methods?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_3|8", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Methods] Line 406: Citation 61 is not complete so please include additional details.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_3|9", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Methods] Line 411: Is Supplementary analysis 3 different than Supplemental Figure S3? If not, terms should be consistent.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_3|10", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "[Methods] Figure S2 and S4 are not referenced in the manuscript.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_3|11", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "What is the sample size for these GPS and VHF collars that had >1000 GPS or VHF locations? It is difficult to assess if every bear that hair collected during capture was analyzed (so sample size reflected in first line of the Results) or if the Environmental similarity was based on a subsample of this assuming GPS/VHF collars failed, bears died, etc., thus a smaller sample size than what was originally collared and had hair collected. Line 431-432 is not adequate to inform the reader of the sample size that this entire section and analysis was based.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_3|12", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "95% kernel density estimator – This estimator is lacking considerable information considering it was done with both autocorrelated GPS data and likely not autocorrelated data with VHF telemetry. The program used for the kernel density estimator should be included as well as the smoothing option would be a minimum amount of information needed here. It would also be helpful to understand the reason for this choice if it was to “extract habitat composition in each bear’s lifetime home range.” Do the authors believe this is the best choice of an estimator considering it has been documented to be one of these least representative estimators of home range across many species?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|70|Human_3|13", "source": "prb", "split": "test", "paper_id": "prb70", "comment": "Extracting home range composition for the “median” year if multiple years were monitored needs additional details. This might be appropriate for bears monitored 1-3 years but if monitored 5-10 years I question the reliability of the Corine Landcover Maps specifically if they are static and collected/released annually or in 5 year intervals? The lack of details on this data source makes this difficult to evaluate.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|Claude|1", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "The paper reports genomic prediction accuracies that decline substantially when moving from 5-fold cross-validation to external validation with the recent hybrids panel. For several traits, this decline is dramatic (e.g., Leaf Expansion Rate drops from r=0.77 to r=0.33; rh_PAD drops from r=0.65 to r=0.39), suggesting that cross-validation results may overestimate the practical predictive ability of the models for use in breeding populations with elite genotypes.\n\n\"In c, r=0.57, p = 2.20E-16, CV_RMSE = 5.2%. In d, r=0.53, p = 0.00013, CV_RMSE = 2.8%\"\nThe Figure 1 caption reports cross-validation correlation of r=0.57 for LAR, which drops slightly to r=0.53 in external validation. This modest decline is acceptable. However, the supplementary data reveals far more problematic declines for other traits.\nFrom Supplementary Table 5: \"Leaf Expansion Rate (max LER) ... Mean r 0.77 ... [External validation] r 0.33\"\nThe dramatic decline from r=0.77 in cross-validation to r=0.33 in external validation for LER represents a loss of approximately 57% of the predictive correlation. This is a substantial reduction that indicates the cross-validation results may not reflect real-world predictive utility for elite breeding populations. A correlation of r=0.33 explains only about 11% of variance, which has limited practical value for breeding decisions.\nFrom Supplementary Table 5: \"rh_PAD (relative height at 50% of leaf area) ... Mean r 0.65 ... [External validation] r 0.39\"\nThe architecture trait rh_PAD shows a decline from r=0.65 to r=0.39, representing a 40% reduction in predictive correlation. The CV_RMSE also increases substantially from 9.4% to 15.8%, indicating degraded prediction quality.\n\"the panel of recent hybrid varieties provided less accurate results, but correlations between predicted and observed values still ranged from 0.33 to 0.71 and mostly with significant p-values\"\nThe paper acknowledges the lower accuracy in external validation but frames it positively. However, literature on genomic selection clearly establishes that cross-validation can inflate accuracy estimates when population structure is present. The decline observed here is consistent with known pitfalls where cross-validation accuracy does not translate to practical breeding applications.\n\"Genomic prediction accuracies obtained from random cross validation can be strongly inflated due to population or family structure, a characteristic shared by many experimental plant populations and breeding populations.\" [[1]](#citation-list)\nThis external reference confirms that the substantial accuracy declines observed in this paper from cross-validation to external validation are a known phenomenon that can lead to overestimation of practical predictive ability.\n\nReferences:\n[1] Lian L, de Los Campos G. (2021). [How Population Structure Impacts Genomic Selection Accuracy in Cross-Validation: Implications for Practical Breeding.](https://pmc.ncbi.nlm.nih.gov/articles/PMC7772221/) Frontiers in Plant Science, 11:592977.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|Claude|2", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "The paper compares rh_PAD (relative height at 50% of leaf area from 3D reconstruction) measured indoors with ALA (Average Leaf Inclination Angle derived from PROSAIL model inversion) measured in the field, treating these as equivalent architectural traits. However, these are fundamentally different measurements based on different physical principles, and no validation is provided to demonstrate they capture the same genetic variation in plant architecture.\n\n\"Plant architecture is a more difficult case because its measurement relies on different principles in indoor vs field experiments\"\nThe authors explicitly acknowledge that these traits are measured using different principles, yet they proceed to correlate them and draw conclusions about indoor-field transferability. The indoor trait (rh_PAD) measures the vertical distribution of leaf area from 3D reconstruction, while the field trait (ALA) measures average leaf inclination angle from radiative transfer model inversion. These capture different aspects of plant architecture.\n\"The architectural trait considered indoor (rh_PAD) was derived from 3D reconstructions of individual plants, via the difference in altitude between the top of the plant and the point where half of leaf area is reached, normalized by plant height\"\nrh_PAD is a normalized height measurement describing where leaf area is concentrated along the plant stem. This is conceptually distinct from leaf angle.\n\"ALA (Average Leaf inclination Angle to the soil level) ... was calculated by inversion of the PROSAIL model\"\nALA measures the average angle of leaves relative to the soil. While both traits relate to light interception, they describe different geometric properties of the canopy. A plant could have leaves concentrated at a certain height (affecting rh_PAD) with varying angles (affecting ALA), or vice versa.\n\"In e, rho=0.34, p = 0.031 (r=0.28, p=0.08)\"\nThe external validation for the rh_PAD to ALA comparison shows a non-significant Pearson correlation (r=0.28, p=0.08) while the Spearman correlation is significant (rho=0.34, p=0.031). The authors report the significant Spearman result, but the non-significant Pearson correlation suggests limited linear relationship between predicted rh_PAD and observed ALA, raising questions about whether these traits are truly equivalent measures of the same underlying architecture.\n\"In this research, we fixed the ALA (average leaf angle) to an overall mean value for generating synthetic datasets as it is difficult to determine ALA accurately, which conflicts with the fact/knowledge that the variable ALA was reported to significantly affect canopy reflectance\" [[2]](#citation-list)\nExternal literature confirms that ALA retrieval from PROSAIL model inversion has inherent difficulties and uncertainties, further questioning whether ALA can reliably serve as a field proxy for indoor architectural measurements.\n\nReferences:\n[2] Verrelst J, Rivera JP. (2017). Integration of a physiologically-based model into global satellite-based spectral retrievals. Cited in: [Integrating a crop growth model and radiative transfer model...](https://pmc.ncbi.nlm.nih.gov/articles/PMC9629788/) Agricultural and Forest Meteorology, 2022.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|Claude|3", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "Stomatal conductance (gs_max) is presented as one of the key adaptive traits for climate resilience, yet the paper provides no external validation data for genomic prediction of this trait. The supplementary materials explicitly state \"Missing data\" for external validation of stomatal conductance, making it impossible to assess whether genomic predictions trained on indoor measurements would transfer to independent populations.\n\n\"Breeding for resilience to climate change requires considering adaptive traits such as plant architecture, stomatal conductance and growth\"\nThe abstract specifically highlights stomatal conductance as one of the key adaptive traits for climate resilience, establishing its importance to the paper's central claims.\n\"physiological traits involved in plant response to heat and drought, such as leaf growth rate or stomatal conductance, have not been improved over the last 60 years of maize selection\"\nThe introduction emphasizes that stomatal conductance is an important trait that has not been improved through breeding, making it a priority target for the proposed approach. The lack of external validation for this trait is therefore particularly problematic for the paper's stated goals.\nFrom Supplementary Table 5: \"Stomatal conductance (gs max) ... 302 ... 0.55 ... 0.53 ... [External Validation] Missing data\"\nThe supplementary table explicitly shows \"Missing data\" for external validation of stomatal conductance. While cross-validation shows r=0.55, the absence of external validation makes it impossible to determine whether this prediction accuracy would hold in an independent population, especially given the substantial accuracy declines observed for other traits (e.g., LER dropping from r=0.77 to r=0.33).\n\"the genotypic values of stomatal conductance derived from this approach correlated with those obtained via classical leaf gas exchange, when the same plants were measured with both techniques\"\nWhile the paper validates the indoor measurement method against classical leaf gas exchange (same plants, same environment), this does not address whether genomic predictions of stomatal conductance would transfer to field conditions or independent breeding populations—the key question for practical application.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|Claude|4", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "Several key indoor-field comparisons are based on very small sample sizes (n=18-20 hybrids), which limits statistical power and produces correlation estimates with wide confidence intervals. These small sample sizes make it difficult to reliably assess the strength of indoor-field relationships.\n\n\"A subset of 20 hybrids of the 'recent hybrids' panel was evaluated in one experiment during winter 2021, with three replicates per hybrid\"\nThe recent hybrids panel, which serves as the external validation set, includes only 20 hybrids evaluated indoors. This sample size is substantially smaller than is typically recommended for genomic prediction validation studies.\nFrom Supplementary Table 4: \"rh_PAD Indoor VS ALA Field 4 ... 18 ... r=0.58, p=0.0118\"\nThe indoor-field comparison for the architectural trait is based on only 18 common hybrids. With such a small sample size, the correlation estimate of r=0.58 has considerable uncertainty, and single outliers could substantially influence the results.\nFrom Supplementary Table 4: \"rh_PAD Indoor VS ALA Field 2 ... 18 ... r=0.60, p=0.0085\"\nAnother indoor-field architecture comparison based on only 18 hybrids. The 95% confidence interval for a correlation of r=0.60 with n=18 spans roughly from 0.15 to 0.85, indicating substantial uncertainty in the true correlation strength.\n\"The effect of the training population size was explored. Some hundred individuals closely related to the breeding population were found to be able to yield the highest prediction accuracies.\" [[3]](#citation-list)\nLiterature on genomic prediction training population optimization suggests that several hundred individuals are typically needed to achieve reliable prediction accuracies. The external validation sample of 20 hybrids falls well below this threshold.\n\"Gene signatures generated from small datasets should be interpreted with caution as they may not be reproducible\" [[4]](#citation-list)\nWhile this reference addresses gene expression prediction, the general principle applies: small sample sizes in training and validation can produce unreliable and irreproducible results, making the correlations reported in this paper for comparisons with n<30 potentially unstable.\n\nReferences:\n[3] Arojju SK et al. (2017). [Optimizing Training Population Size and Genotyping Strategy for Genomic Prediction Using Association Study Results and Pedigree Information.](https://journals.plos.org/plosone/article?id=10.1371/journal.pone.0169606) PLOS ONE, 12(1):e0169606.\n[4] Stretch C et al. (2013). [Effects of Sample Size on Differential Gene Expression, Rank Order and Prediction Accuracy of a Gene Signature.](https://pmc.ncbi.nlm.nih.gov/articles/PMC3670871/) PLOS ONE, 8(6):e65380.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|Claude|5", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "The paper acknowledges that ALA (Average Leaf Angle) values and heritability are \"very sensitive to crop phenological stage,\" but the indoor-field comparisons rely on ALA measurements at specific phenological stages without demonstrating that the timing of field measurements was consistently matched across experiments or that temporal variation was adequately controlled.\n\n\"Notably, ALA values and heritability were very sensitive to crop phenological stage whereas those of rh_PAD were more stable\"\nThe authors explicitly acknowledge temporal sensitivity of ALA measurements. If ALA varies substantially with phenological stage, then the observed correlations with rh_PAD could be confounded by differences in measurement timing across experiments and genotypes.\n\"ALA: average leaf angle estimated at flowering time from UAV images, via inversion of the model PROSAIL\"\nWhile the paper states ALA was measured \"at flowering time,\" flowering time varies among genotypes, potentially introducing systematic bias where early-flowering and late-flowering genotypes are compared at different physiological ages or under different environmental conditions.\n\"UAV flights were performed three times in one experiment of the 'genetic progress' panel during the period from plant emergence to flowering, and seven times in two experiments for the 'recent hybrids' panel during the same period\"\nMultiple UAV flights were conducted, but the paper does not clearly explain how phenological stage was controlled when selecting which ALA measurements to use for comparisons, or whether variation among measurement dates contributed to the observed variance.\n\"The PROSAIL validation to retrieve LAI from hyperspectral imagery showed a R² value of 0.5 against ground LAI with RMSE of 0.8 m²/m²\" [[5]](#citation-list)\nExternal validation studies of PROSAIL model inversion show moderate accuracy (R²=0.5) for LAI retrieval in maize. Similar uncertainties likely affect ALA retrieval, which combined with phenological sensitivity, suggests that field ALA measurements carry substantial measurement error that could attenuate correlations with indoor measurements.\n\nReferences:\n[5] Kayad A et al. (2022). [Retrieving maize LAI to access biomass and grain yield from UAV multi-spectral imagery.](https://repository.cimmyt.org/bitstream/10883/22017/1/65070.pdf) Field Crops Research, 282:108449.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|GPT|1", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "The paper’s genomic-prediction evaluation likely overstates predictive ability because the described 5-fold cross-validation does not enforce independence with respect to family/relatedness structure (Validity, Conclusions), particularly in panels with strong genomic relatedness (Methods: “Training and validation schemes of genomic predictions”, Supplementary Fig. 3).\n\n“Each training set was sampled randomly but proportionally to ‘diversity panel’ genetic groups and across years of release of ‘genetic progress’ hybrids (Supplementary Fig. 4). This sampling method was chosen to maintain a good coverage of the total genetic space covered by the training set.”\nThis describes a random (though stratified) split that aims for representativeness, not a split that prevents close relatives from appearing in both train and test folds. In genomic prediction, random CV in structured or family-based populations can substantially inflate reported correlations because the model can leverage realized relatedness rather than learning stable marker–QTL LD that transfers to genuinely novel genetic backgrounds. The paper does not report a “leave-family-out”, “leave-group-out”, or forward-in-time CV scheme that would better emulate the intended breeding use case of predicting new elite material. Because the manuscript interprets these CV correlations as evidence of “good” genomic predictability, the evaluation design is central to the validity of that claim. Without a stricter split, the reported r values cannot be confidently interpreted as generalizable prediction accuracy beyond the relatedness present in these panels. This is a major concern because the paper’s downstream conclusions explicitly advocate using these predictions for selection decisions.\n“The representation of the diversity panel hybrids corresponding to the lines crossed with UH007, highlights the effect of the common parent UH007, which induces a strong genomic relatedness between the diversity panel hybrids and separates them from the other panels following the first PCoA dimension.”\nThis explicitly documents strong relatedness induced by the common parent UH007, meaning many hybrids share substantial genome segments by design. In such a context, random CV that mixes these related genotypes across folds can yield optimistic accuracy estimates because test individuals are not independent of training individuals in terms of realized genomic relationships. The paper does not show that prediction performance remains similar when blocking on this family structure (e.g., leaving out subsets of dent lines or grouping by pedigree/PCoA clusters). This matters directly for the paper’s claims about deploying genomic prediction for ranking genotypes, because practical breeding often requires accurate within-family and across-cycle predictions, not just across-family mean differences. The supplementary statement therefore strengthens the inference that the CV protocol, as described, is vulnerable to relatedness-driven inflation. Consequently, the reported “good” predictive abilities are not yet a robust basis for the manuscript’s selection-oriented conclusions.\n“However, genomic prediction accuracies obtained from random cross validation can be strongly inflated due to population or family structure, a characteristic shared by many breeding populations.” [[1]](https://pmc.ncbi.nlm.nih.gov/articles/PMC7772221/)\nThis sentence directly states the key methodological risk associated with using random CV in structured breeding populations: inflated accuracy. The population structure described in the reviewed paper (including a common parent and clear structure in Supplementary Fig. 3) matches the conditions under which inflation is expected. Therefore, the manuscript’s reliance on a random/stratified CV split without demonstrating robustness under family-blocked splits undermines the validity of its reported predictive correlations. The cited work also emphasizes that random CV may be useful for model comparison but does not necessarily represent accuracy expected in practical breeding, aligning with the concern here. The reviewed paper’s claims are framed in a breeding-decision context, so the distinction between “random CV accuracy” and “practical forward prediction accuracy” is not a minor nuance but a core validity issue. This evidence from the literature supports treating the CV design as a publication-limiting methodological gap unless addressed.\n“This study shows that markers can capture genetic relationships among genotyped animals, thereby affecting accuracies of GEBVs.” [[2]](https://pmc.ncbi.nlm.nih.gov/articles/PMC2219482/)\nThis sentence highlights a specific mechanism by which prediction accuracy can appear high even when it primarily reflects relatedness rather than causal marker–trait association that transfers broadly. In the reviewed manuscript, the training and test folds (and even the external validation set) can share substantial relatedness, as indicated by the UH007-induced structure and overlap among panels. If accuracies are partly driven by relationship capture, they may not hold when predicting less-related elite material or new breeding cycles. The reviewed paper does not separate “accuracy due to relationships” from “accuracy due to LD” (e.g., by using validation sets intentionally distant in relatedness or by analyzing accuracy decay across cycles). Because the paper uses these accuracies to justify using genomic prediction for selecting “spender” vs “conservative” ideotypes, failing to address this mechanism threatens the validity of its practical recommendations. The literature quote therefore supports that the manuscript’s CV results are not sufficient, as presented, to justify the claimed predictive utility.\n\nReferences:\n[1] [Werner et al., “How Population Structure Impacts Genomic Selection Accuracy in Cross-Validation: Implications for Practical Breeding Programs” (Frontiers in Plant Science, 2020)](https://pmc.ncbi.nlm.nih.gov/articles/PMC7772221/)\n[2] [Habier et al., “The Impact of Genetic Relationship Information on Genome-Assisted Breeding Values” (Genetics, 2007)](https://pmc.ncbi.nlm.nih.gov/articles/PMC2219482/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|GPT|2", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "The manuscript’s conclusions about inferring adaptive trait values across diverse field environments are not robust because the genomic prediction target is defined as “trait genotypic means (BLUEs over experiments)” rather than environment-specific responses (Conclusions, Validity), and the prediction framework does not model genotype-by-environment interaction despite repeatedly emphasizing environment dependence.\n\n“We show that maize adaptive traits can be inferred in different fields, based on genotypic values obtained indoor and on environmental conditions in each considered field. The modelling of environmental effects allowed translation from indoor to fields, but also from one field to another field.”\nThis is a central claim: trait inference is presented as field- and environment-specific, relying on environmental conditions. Such a claim requires either (i) environment-specific prediction models or (ii) a reaction-norm/interaction framework showing that predicted genotypic differences persist appropriately across varying conditions. However, the manuscript’s genomic prediction section evaluates prediction of genotypic means rather than explicit environment-conditioned trait values, so it does not directly validate the stated “in different fields” inference claim. Without modeling G×E, the reported correlations can mainly indicate an average genetic tendency across environments, which is not equivalent to predicting performance under a particular field scenario. This gap matters because adaptive traits (e.g., stomatal conductance, leaf growth) are explicitly discussed as highly sensitive to environmental drivers in the introduction, so averaging can hide important crossover interactions. Therefore, the abstract’s field-specific inference language is not supported by a matching environment-aware genomic prediction evaluation. This weakens the robustness of the paper’s adaptation-oriented conclusions.\n“where y is the vector of trait genotypic means (BLUEs over experiments) of n hybrids”\nThis sentence defines the response variable for genomic prediction as an across-experiment mean, not an environment-indexed phenotype or a set of environment-specific BLUEs/BLUPs. For traits with substantial genotype × environment interaction (a major motivation of the study), collapsing across experiments can reduce apparent variability and artificially simplify the prediction task. It also prevents the reader from knowing whether the same genomic model can predict trait expression under particular environmental covariates, which is the core practical question for “adaptive traits in the field.” The paper does not report whether BLUEs were computed separately per field and then predicted per field, nor does it present prediction accuracy stratified by environmental conditions or by stress regime. Consequently, the genomic prediction results cannot be straightforwardly interpreted as validating environment-specific trait inference or field-to-field translation. This is a major methodological mismatch between the study’s stated objective (field translation under varying environments) and the prediction target actually evaluated (a pooled mean). As a result, the conclusions about deploying genomic prediction for future climates are less supported than implied.\n“In most agricultural crops the effects of genes on traits are modulated by environmental conditions, leading to genetic by environmental interaction (G × E).” [[3]](https://pmc.ncbi.nlm.nih.gov/articles/PMC3931944/)\nThis sentence summarizes the widely accepted reason why environment-specific modeling is necessary when the goal is prediction across heterogeneous field conditions. The reviewed manuscript itself motivates the work by emphasizing high environmental sensitivity and large G×E, but then evaluates genomic prediction on environment-averaged BLUEs. That evaluation cannot establish whether genomic predictions remain accurate when conditions change, which is exactly what G×E implies. The cited work treats G×E as a central feature of crop traits and uses models that incorporate environmental information and interactions to improve prediction; this contrasts with the reviewed manuscript’s mean-only target for genomic prediction. Therefore, the literature supports that ignoring G×E (or not evaluating it) is a substantive limitation when making claims about adaptation across fields. This is not a minor modeling choice but a critical determinant of whether predictions transfer between environments, which is central to the paper’s stated contribution. The mismatch indicates that the manuscript’s adaptation conclusions are less robust than they appear.\n“In principle, G × E can be accounted for using interactions between markers and environmental covariates (ECs).” [[3]](https://pmc.ncbi.nlm.nih.gov/articles/PMC3931944/)\nThis sentence provides a concrete, established modeling route for the exact problem the reviewed paper highlights—predicting trait expression under varying environmental conditions. The reviewed paper records environmental variables in field experiments and uses environmental drivers in the indoor-to-field translation for some traits, so the necessary ingredients for interaction-aware genomic prediction appear available in principle. Yet the genomic prediction model described is a GBLUP-AD on pooled BLUEs without environmental covariates, and the evaluation does not test a marker-by-environment or marker-by-covariate framework. As a result, the manuscript does not validate whether genomic prediction can support the claimed translation “from one field to another field” in an environment-aware way. The literature quote underscores that this omission is methodologically consequential, not optional, when the aim is field-specific prediction. Including and evaluating such interaction models is common practice in modern multi-environment genomic prediction studies, so its absence reduces confidence in the manuscript’s field-adaptation conclusions. This evidence supports the claim that the current genomic prediction results do not sufficiently back the paper’s stated adaptation contribution.\n\nReferences:\n[3] [Jarquín et al., “A reaction norm model for genomic selection using high-dimensional genomic and environmental data” (Theoretical and Applied Genetics, 2014)](https://pmc.ncbi.nlm.nih.gov/articles/PMC3931944/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|GPT|3", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "The paper’s field-derived architectural (ALA) and LAI measurements—central to its indoor-to-field comparisons—are produced via PROSAIL inversion without reporting the inversion configuration, constraints, or retrieval uncertainty, which is problematic because radiative transfer model inversion is ill-posed (Validity, Data and methodology), undermining confidence in the reported correlations and ranking consistency.\n\n“The architectural trait ALA (Average Leaf inclination Angle to the soil level) and Leaf Area Index (LAI) were calculated by inversion of the PROSAIL model, based on multispectral images of field UAV flights.”\nThis statement indicates that key “field” variables are not directly measured but inferred through an inversion pipeline, yet the manuscript does not specify essential elements of that inversion (e.g., parameter bounds, priors, soil/background handling, objective function, regularization, or identifiability safeguards). Because ALA and LAI are later treated as genotypic values used for correlation analyses, quartile assignment, and claims of consistency between environments, the accuracy and uncertainty of these inversions materially affect the validity of the conclusions. Multispectral UAV data provide limited spectral information compared to hyperspectral settings, which typically increases parameter confounding and reliance on strong priors. Without reporting inversion settings, a reader cannot reproduce the ALA/LAI estimates or assess whether the inversion could systematically bias genotypes (e.g., via phenology-dependent reflectance changes or canopy closure effects). The paper also does not provide uncertainty intervals or sensitivity analyses for ALA/LAI retrieval, despite using them as if they were ground-truth phenotypes. This lack of transparency and uncertainty treatment is therefore a major methodological weakness, not merely a reporting omission.\n“We compared (i) measured values in the field, obtained via UAV imaging and the inversion of the PROSAIL radiative transfer model with (ii) the LAI simulated by a crop model … The correspondence between measured and estimated LAI … suggested that this approach is promising (r=0.63, Fig. 4, Supplementary Table 4).”\nHere, the manuscript frames PROSAIL-inverted LAI as “measured values in the field,” yet it is model-derived and thus carries inversion error and modeling assumptions that should be propagated into downstream comparisons. The reported agreement (r = 0.63) is only interpretable if the uncertainty and bias of the PROSAIL-derived LAI are characterized; otherwise, an apparent mismatch could be due to either the crop model, the inversion, or both. Because the LAI comparison is used as evidence that indoor upstream traits plus environmental data can infer a key field trait, unquantified inversion error undermines the strength of this evidence. Additionally, Supplementary Table 4 reports a large relative error for this comparison (CV_RMSE = 22.9%), which further elevates the importance of uncertainty reporting and validation. Common practice in remote-sensing retrieval papers is to report validation against ground measurements and/or retrieval uncertainties, especially when inversion outputs are used as phenotypes. The manuscript does not provide such validation details here, so the “promising” claim is not sufficiently supported for a major, model-mediated result.\n“A limitation shared by all of the physically based models is the ill-posed nature of model inversion … the fact that different combinations of canopy parameters may correspond to almost similar spectra.” [[5]](http://www.international-agrophysics.org/pdf-104131-35199?filename=Comparative-evaluation-of.pdf)\nThis sentence states a core reason why inversion outputs require careful specification of constraints and uncertainty: multiple parameter settings can reproduce similar reflectance. The reviewed manuscript uses inversion to recover canopy-structure variables (ALA and LAI), which are precisely the types of parameters that can be confounded in PROSAIL inversions, especially with limited-band multispectral data. Therefore, the absence of inversion details and uncertainty quantification is not merely incomplete reporting; it directly limits the reader’s ability to evaluate whether retrieved ALA/LAI values are identifiable and comparable across dates and sites. The ill-posedness implies that small changes in priors, parameter bounds, or cost functions can yield different retrieved trait values, potentially altering genotype rankings. Because the paper’s claims hinge on genotype ranking consistency and correlations between indoor and field-derived values, sensitivity to inversion choices could materially change conclusions. The cited literature thus supports treating inversion transparency and uncertainty as publication-critical for claims built on PROSAIL outputs. In this context, the manuscript’s current reporting is insufficient to establish validity.\n“The ill-posed problem results from different combinations of model parameters contributing to highly similar canopy reflectance spectra.” [[4]](https://www.sciopen.com/local/article_pdf/10.1016/j.cj.2022.04.003.pdf)\nThis sentence reinforces that ill-posedness is not an abstract concern but a practical property of RTM inversions that arises from parameter non-uniqueness. In the reviewed paper, both ALA and LAI are inferred simultaneously from canopy reflectance via inversion, which is a setting where parameter trade-offs are common and can be exacerbated by multispectral limitations. Because the manuscript compares genotypic values derived from these inversions to indoor traits and uses them in downstream statistical summaries, unreported inversion uncertainty can translate into overconfidence in correlation coefficients and quartile assignments. The literature also emphasizes that attempts to address ill-posedness often involve constraining parameter ranges, avoiding unrealistic combinations, and using priors—choices that must be documented to make results interpretable and reproducible. The reviewed manuscript does not provide those inversion choices, so it is unclear whether the retrieved ALA/LAI are stable across phenological stages and field conditions. As a result, the validity of architecture/LAI comparisons that depend on PROSAIL inversion is weakened. This literature evidence supports the claim that the paper should not treat PROSAIL-inverted variables as unquestioned ground truth without transparent inversion specification and uncertainty reporting.\n\nReferences:\n[4] [Sun et al., “Leaf pigment retrieval using the PROSAIL model: Influence of uncertainty in prior canopy-structure information” (The Crop Journal, 2022)](https://www.sciopen.com/local/article_pdf/10.1016/j.cj.2022.04.003.pdf)\n[5] [Mridha et al., “Comparative evaluation of inversion approaches of the radiative transfer model for estimation of crop biophysical parameters” (International Agrophysics, 2015)](http://www.international-agrophysics.org/pdf-104131-35199?filename=Comparative-evaluation-of.pdf)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|GPT|4", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "The manuscript’s plant-architecture component does not convincingly establish that indoor and field genotypic values “match” because it correlates different traits (rhPAD vs ALA) and the independent validation exhibits weak rank agreement (Validity, Conclusions), undermining the claim that indoor platform measurements can be reliably translated to field-relevant architecture for selection.\n\n“The genotypic values of ALA measured in the field were well correlated to those of rhPAD measured in a phenotyping platform … The same applied to 20 hybrids of the ‘recent hybrids’ panel in two field experiments, with good relationships between rhPAD and ALA … Notably, ALA values and heritability were very sensitive to crop phenological stage whereas those of rhPAD were more stable.”\nThis passage acknowledges that the indoor and field quantities are different (rhPAD cannot be measured in the field; ALA is derived in the field), and it further notes that ALA is highly stage-sensitive, which is a red flag for using it as a stable genotype descriptor. Correlation between two related but distinct traits does not establish that genotypic values “match” in the sense required for robust translation; it only indicates association under specific measurement conditions and developmental stages. The statement that ALA is phenology-sensitive implies that the same genotype could shift relative position depending on measurement timing, complicating breeding use where consistent rank ordering is crucial. The manuscript does not show that the rhPAD–ALA mapping remains stable across phenological windows or across environments, beyond a small number of fields and limited sample sizes (n as low as 18 in Supplementary Table 4). Because the paper uses this architecture link as evidence that indoor phenotyping can inform field-adaptive trait values, instability in the field-derived proxy (ALA) weakens the translation claim. Consequently, the evidence presented is insufficient to support the strong interpretation that indoor architecture “matches” field architecture in a selection-ready way.\n“Irrelevant (two different traits compared)”\nThis explicit note in Supplementary Table 4 appears in the row comparing rhPAD (indoor) against ALA (field), signaling that at least some standard comparison metrics (e.g., RMSE) are not meaningful because the quantities are not the same trait. That admission directly conflicts with interpreting the correlation as a measurement-equivalence validation; correlation alone cannot substitute for demonstrating that the same construct is being measured. If the traits are different enough that error metrics are “irrelevant,” then conclusions phrased as “genotypic values matched between indoor and field conditions” (as in the abstract) are at risk of overstating what was shown. The manuscript does not provide a mechanistic or calibration model that maps rhPAD to ALA with quantified predictive uncertainty, which would be the appropriate way to justify cross-trait translation. Instead, it relies on correlation coefficients that can be sensitive to maturity-group structure and phenology timing (which the paper itself flags). Therefore, the supplementary note is strong internal evidence that the architecture comparison is not a like-for-like validation and should be interpreted more cautiously. This undermines the validity of using this comparison as a key pillar of indoor-to-field “matching” for plant architecture.\n“In e, rho=0.34, p = 0.031 (r=0.28, p=0.08).”\nThis is the manuscript’s independent (external) validation statistic for the architecture link, and it indicates weak rank correlation (rho = 0.34) and a non-significant Pearson correlation (r = 0.28, p = 0.08). For breeding use, rank-based agreement is often more relevant than raw correlation because selection is made by ordering genotypes; a rho of 0.34 implies substantial reordering. Moreover, the paper’s own framing emphasizes “adequate ranking” and conservation of quartiles as “a necessary condition for breeding,” so weak rank agreement directly contradicts the operational claim. The low external-validation strength also suggests that whatever association exists in the training/cross-validation setting does not transfer reliably to elite recent hybrids, which the paper highlights as a key target group. Because this statistic is presented as part of the central architecture figure, it materially weakens the conclusion that indoor phenotyping plus genomic prediction can support field-relevant architecture ranking. Therefore, the independent-validation evidence does not support the manuscript’s stronger translation language and should have led to a more cautious conclusion.\n“Leaf pigments are critical indicators of plant photosynthesis, stress, and physiological conditions. Inversion of radiative transfer models (RTMs) is a promising method … and adding prior information has been effective in alleviating the ‘ill-posed’ problem, a major challenge in model inversion. Canopy structure parameters, such as leaf area index (LAI) and average leaf inclination angle (ALA), can serve as prior information …” [[4]](https://www.sciopen.com/local/article_pdf/10.1016/j.cj.2022.04.003.pdf)\nThis quote contextualizes ALA as a canopy-structure parameter within RTM-based inversion workflows and explicitly highlights ill-posedness as a “major challenge” in inversion. In the reviewed manuscript, ALA itself is retrieved via PROSAIL inversion and then used as the field-side proxy for architecture, which means the architecture comparison inherits inversion-related uncertainty and potential instability. The literature emphasizes that priors and constraints are often needed to make inversions workable; the reviewed paper does not detail such constraints for its ALA retrieval, limiting confidence in the stability of ALA-derived genotype rankings. Because the manuscript’s architecture claim depends on correlations between a directly reconstructed indoor metric (rhPAD) and an inverted field metric (ALA), inversion ill-posedness compounds the difficulty of interpreting cross-trait correlations as evidence of biological equivalence. This is especially pertinent given the manuscript’s own statement that ALA is phenology-sensitive, which can interact with inversion assumptions (e.g., canopy closure and spectral saturation effects). Therefore, the literature supports that strong claims about cross-trait matching and rank transfer require careful inversion specification and uncertainty treatment, which are lacking here. This evidence strengthens the conclusion that the architecture “match” is not sufficiently established.\n\nReferences:\n[4] [Sun et al., “Leaf pigment retrieval using the PROSAIL model: Influence of uncertainty in prior canopy-structure information” (The Crop Journal, 2022)](https://www.sciopen.com/local/article_pdf/10.1016/j.cj.2022.04.003.pdf)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|GPT|5", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "The paper’s breeding-oriented conclusion that genotype rankings are “essentially conserved” between indoor and field conditions is not supported by the reported quartile-overlap frequencies and error magnitudes (Conclusions, Appropriate use of statistics), indicating substantial misclassification risk for selection decisions.\n\n“Importantly, the ranking of hybrids and their distribution in highest and lowest quartiles were essentially conserved between indoor and field conditions, a necessary condition for breeding (Supplementary Table 4).”\nThis sentence makes a strong, decision-relevant claim: that rank and quartile assignments are “essentially conserved,” and it frames that as “necessary” for breeding. Because this is a high bar tied to selection decisions, it should be supported by high quartile-overlap rates (especially for the top quartile) and/or by explicit selection-metric analyses (e.g., expected response to selection, precision–recall for top-k selection). The manuscript refers to Supplementary Table 4 as support but does not state what overlap values would count as “essentially conserved” or quantify the expected selection error. Without such thresholds or decision-analytic framing, the statement reads as a qualitative overinterpretation of moderate overlap numbers. Furthermore, the comparisons often involve small numbers of common hybrids (down to 18), which can make quartile overlaps volatile and less reliable for operational claims. Since the paper repeatedly argues for practical breeding utility, overstating rank conservation materially affects the credibility of the conclusions. Therefore, the claim requires stronger quantitative support than what is presented.\n```html\n  <tr>\n    <td rowspan=\"2\">LAR (Leaf Appearance Rate)</td>\n    <td rowspan=\"2\">leaf/ day<sub>20°C</sub></td>\n    <td>Indoor VS Field 3</td>\n    <td>21</td>\n    <td>0.57</td>\n    <td>0.0066</td>\n    <td>0.42</td>\n    <td>0.0587</td>\n    <td>0.259</td>\n    <td>0.020</td>\n    <td>7.7%</td>\n    <td>-0.012</td>\n    <td>-4.5%</td>\n    <td>0.60</td>\n    <td>0.40</td>\n  </tr>\n  ```\nThis table row contains the manuscript’s own quartile-overlap metrics (FSA) for LAR between indoor and Field 3. An FSA of 0.60 for the highest quartile means that a large fraction of top-quartile genotypes are not consistently identified across conditions, and the lowest-quartile overlap is even weaker (0.40). Such overlap rates do not align with the manuscript’s wording “essentially conserved,” which implies near-preservation of rank strata for selection. In breeding contexts, misclassifying a substantial portion of the top or bottom quartile can materially reduce realized gain and can lead to discarding promising genotypes or advancing suboptimal ones. The paper does not translate these FSA values into selection-efficiency metrics (e.g., expected response to selection or top-k precision), so the practical impact is not quantified. Therefore, the reported FSA values themselves argue for a more cautious, less selection-ready interpretation of rank conservation than the manuscript presents.\n```html\n  <tr>\n    <td>LAI (Leaf Area Index)</td>\n    <td>unitless</td>\n    <td>LAI Indoor (+Crop model) VS LAI Field 5 (UAV)</td>\n    <td>47</td>\n    <td>0.63</td>\n    <td>2.16E-06</td>\n    <td>0.66</td>\n    <td>4.63E-07</td>\n    <td>4.42</td>\n    <td>1.02</td>\n    <td>22.9%</td>\n    <td>-0.78</td>\n    <td>-17.6%</td>\n    <td>0.45</td>\n    <td>0.61</td>\n  </tr>\n  ```\nThis table row reports both a large relative error (CV_RMSE = 22.9%) and a low top-quartile overlap (FSA highest quartile = 0.45) for the LAI translation comparison. A CV_RMSE of this magnitude implies that absolute prediction errors are substantial relative to the trait mean, which can readily reshuffle genotype ranks, especially when phenotypic variability is small in elite material. A top-quartile overlap below 0.5 indicates that more than half of “selected” top-quartile genotypes would differ depending on whether one uses field UAV/PROSAIL LAI or the indoor+crop-model estimate, which is problematic for selection decisions. The manuscript labels this approach “promising” and uses it to argue that indoor upstream traits plus environmental data can infer field canopy status, but these metrics suggest limited selection reliability as presented. The paper does not provide uncertainty intervals or sensitivity analyses for these overlap and error measures, so the stability of the ranking is not established. Therefore, the manuscript’s broad statement that rankings are consistent between field and indoor-derived values is not supported for LAI by its own reported error and quartile-overlap statistics.\n“Considering that genomic prediction accuracy will have direct implications on setting selection intensity and breeding cycle time in a breeding program, inflated estimates of prediction accuracy can have adverse effects on the outcome of the selection process.” [[1]](https://pmc.ncbi.nlm.nih.gov/articles/PMC7772221/)\nThis sentence explains why over-optimistic ranking or accuracy claims are not merely academic: they can lead to wrong decisions about selection intensity and resource allocation. The reviewed manuscript uses rank- and quartile-based arguments to claim breeding applicability, so it is important that these metrics reflect realistic selection performance. The relatively modest quartile overlaps and large CV_RMSE values reported in Supplementary Table 4 show that selection based on these translated/predicted values may have substantial error. If such performance is presented as “essentially conserved,” breeders could overtrust the method and incur opportunity costs by selecting suboptimal genotypes. The literature quote thus supports treating ranking/accuracy inflation and misclassification risk as a serious conclusions-level issue. It also connects directly to the reviewed paper’s framing around speed breeding and selecting ideotypes, where misranking can compound across cycles. Therefore, the manuscript should either temper its breeding claims or provide stronger decision-analytic validation consistent with the reported overlap/error levels.\n\nReferences:\n[1] [Werner et al., “How Population Structure Impacts Genomic Selection Accuracy in Cross-Validation: Implications for Practical Breeding Programs” (Frontiers in Plant Science, 2020)](https://pmc.ncbi.nlm.nih.gov/articles/PMC7772221/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "The paper inaccurately claims that genomic prediction resulted in \"adequate ranking\" of genotypes for elite varieties, despite the external validation yielding statistically non-significant correlations for key traits.\n\n\"Genomic prediction resulted in adequate ranking of genotypes for the tested traits, although with lesser precision for elite varieties presenting reduced phenotypic variability.\" (Abstract)\nThis claim is contradicted by the statistical results provided in the supplementary material. The term \"adequate\" implies that the predictions are reliable enough for selection, which is not supported by non-significant correlations.\n\"External validation on the panel of recent hybrid varieties provided less accurate results, but correlations between predicted and observed values still ranged from 0.33 to 0.71 and mostly with significant p-values (from 3.2\\times10^{-10} to 0.031)\" (Discussion)\nThis statement is misleading. While some traits had significant p-values, the key adaptive traits highlighted in the study, such as Leaf Expansion Rate (LER) and plant architecture (rhPAD), did not. As shown below, the correlations for these traits were weak and statistically non-significant.\n\"In e, rho=0.34, p = 0.031 (r=0.28, p=0.08).\" (Figure 3 caption)\nFor the architectural trait rhPAD, the Pearson correlation (r=0.28) in the external validation was not statistically significant (p=0.08 > 0.05). Relying on a marginally significant Spearman correlation (rho=0.34) with such a small sample size (n=20) is insufficient to claim \"adequate ranking\".\n\"Hybrid number | 20 ... r | 0.33 ... rho | 0.30\" (Supplementary Table 5, row for Leaf Expansion Rate, External Validation)\nFor Leaf Expansion Rate (LER), the external validation was performed on only 20 hybrids. A Pearson correlation of r=0.33 with n=20 yields a p-value of approximately 0.15 (calculated using a t-test for correlation), which is far from the significance threshold of 0.05. Thus, the prediction ability for this trait in elite hybrids is not statistically different from zero.\n\"The 244‐accession set with high‐*U* values showed significantly higher prediction accuracy than the low‐*U* set for all SAM traits\" [1]\nStandard genomic prediction studies in maize, such as Crossa et al. (2017) [1] and Technow et al. (2012) [3], typically utilize much larger validation sets (e.g., hundreds of genotypes) to ensure robust estimates of prediction accuracy. Using a validation set of only n=20 makes the estimates highly unstable and the conclusions unreliable.\n\nReferences:\n[1] Crossa, J. et al. Genomic prediction of maize microphenotypes provides insights for optimizing germplasm conservation and use. *Plant Genome* **10**, 1-15 (2017). https://doi.org/10.3835/plantgenome2017.04.0033\n[3] Technow, F. et al. Genomic prediction of hybrid performance in maize with models incorporating dominance and population specific marker effects. *Theor. Appl. Genet.* **125**, 1181–1194 (2012). https://doi.org/10.1007/s00122-012-1903-0", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "The paper asserts that stomatal conductance is a key adaptive trait that can be predicted in the field, yet it fails to provide any direct field validation for this trait.\n\n\"We show that maize adaptive traits can be inferred in different fields, based on genotypic values obtained indoor and on environmental conditions in each considered field.\" (Abstract)\nThis general claim implies that all studied traits, including stomatal conductance, were validated in the field. However, the paper offers no evidence for the successful translation of stomatal conductance from indoor to field conditions.\n\"Method field | Not measurable at HTP\" (Table 1, row for Stomatal conductance)\nThe authors explicitly acknowledge that stomatal conductance cannot be measured at high throughput (HTP) in the field. Consequently, there is no \"Method field\" data to validate the indoor measurements or the model predictions.\n\"External Validation (Recent hybrids panel) ... Missing data\" (Supplementary Table 5, row for Stomatal conductance)\nThe external validation for stomatal conductance is completely missing. Without comparing the indoor-modeled values or genomic predictions to actual field data (even on a small subset), it is impossible to confirm that the \"spender or conservative strategies\" identified indoor actually manifest in the field.\n\"Resulting estimations of whole-plant stomatal conductance were well related to leaf stomatal conductance measured via gas exchange\" (Results)\nThe only validation provided is between the indoor whole-plant model and indoor leaf-level gas exchange measurements. This proves internal consistency within the indoor platform but does not address the critical question of whether these values relate to field performance, which is the paper's central premise.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "The paper characterizes the relationships between indoor and field traits as \"close correlations,\" which overstates the strength of the association given the moderate correlation coefficients and low coefficients of determination.\n\n\"We first show that genotypic values of traits measured indoor closely correlate with those in the field\" (Introduction)\nThe term \"closely correlate\" suggests a strong predictive relationship. However, the reported correlations (r) are mostly in the range of 0.5 to 0.6, which corresponds to coefficients of determination (R^2) of only 0.25 to 0.36. This means that indoor traits explain only about 25-36% of the genetic variance in the field, leaving the majority of the variance unexplained.\n\"Correlation indoor vs field ... 0.57 ... 0.63\" (Table 1)\nFor Leaf Appearance Rate (r=0.57) and Leaf Area Index (r=0.63), the correlations are moderate at best. While statistically significant, they are not strong enough to imply that indoor phenotyping can effectively replace field trials or that the traits are \"closely\" aligned without substantial error.\n\"The correlations observed in these three cases between indoor platform and fields are therefore higher (r= 0.57 to 0.78, Table 1) than those reported by Poorter et al. (2016)\" (Discussion)\nThe authors compare their results favorably to a meta-analysis [2], but even r=0.57 is often considered low for high-precision breeding applications where r > 0.8 is desired for accurate selection. Characterizing these as \"close\" misleads the reader regarding the utility of the method for precise ranking. Furthermore, as noted by Monteith (1994) [4] and Tardieu et al. (2017) [5], the translation of indoor traits to field conditions is complex and often requires more than simple correlation to be effective.\n\nReferences:\n[2] Poorter, H. et al. Biomass allocation to leaves, stems and roots: meta-analyses of interspecific variation and environmental control. *New Phytologist* **193**, 30-50 (2012). https://doi.org/10.1111/j.1469-8137.2011.03952.x\n[4] Monteith, J. L. Validity of the correlation between intercepted radiation and biomass. *Agricultural and Forest Meteorology* **68**, 213–220 (1994). https://doi.org/10.1016/0168-1923(94)90037-X\n[5] Tardieu, F., Cabrera-Bosquet, L., Pridmore, T. & Bennett, M. Plant Phenomics, From Sensors to Knowledge. *Current Biology* **27**, R770–R783 (2017). https://doi.org/10.1016/j.cub.2017.05.055", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "The paper does not provide access to the code or data used for the analysis, preventing reproduction of the complex modeling and genomic prediction results.\n\n\"The modelling of environmental effects allowed translation from indoor to fields, but also from one field to another field.\" (Abstract)\nThe study relies heavily on specific implementations of crop models (e.g., modified PROSAIL, Lacube et al. model) and genomic prediction pipelines. Without the source code, it is impossible to verify how the environmental covariates were integrated or how the models were calibrated.\n\"All prediction models were fitted using the Bayesian Generalized Linear Regression (BGLR) R package\" (Methods)\nWhile the package is public, the specific scripts for data processing, cross-validation splitting (which was complex, involving genetic groups), and hyperparameter tuning are not provided.\n\"Supplementary Files ... Supplementaryinformatonbouidghaghen.pdf\" (File list)\nThe supplementary material contains only a PDF with tables and figures. There are no links to a GitHub repository or a data archive (e.g., Zenodo, Dryad) containing the phenotypic data, genotypic data, or analysis scripts, which is a standard requirement for reproducibility in computational biology.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "I think that the above framework should be outlined from the onset and should guide the methods and the presentation of the results. The current version, it somehow does, but in a rather ad-hoc manner. For instance: The estimates in Table 1 are correlations of blues which are not necessarily good estimates of genetic correlations (to do this, you should use a standard methods to estimate genetic correlations). Heritabilities, the other parameter affecting ACC, are mentioned by not fully reported in the main text. And, as noted, there are not reports of the accuracy of indirect selection and the relative efficiency (i.e., the ratio of the accuracy of indirect selection to the accuracy of direct selection). To me, the evidence will be stronger and the presentation clearer if you outline this framework and stick to report estimates of the parameters that are key to evaluate indirect selection.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "I am not sure why are the correlation between phenotypes in different fields that relevant to your argument. I understand that the idea is to show that genetic correlations are below one even for the same trait measured in two different trials (e.g., different locations, different years) but I don’t think this should occupy a central role relative to what I discussed in I.1", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "Genetic correlations, heritabilities, and even the prediction performance in CV are likely to be affected by the structure of the genotypes. The three data sets (particularly the diversity panel and the one based on hybrids that span over decades of release) are likely to have a level of genetic diversity, and possibly structure, that is much higher than the one in current elite line pools. It would be important to: (i) assess population stratification, and (ii) possibly correct by it including in the models used to estimate heritabilities and genetic correlations a few PCs that can control for that.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "When you report estimates (e.g., correlations in Table 1, or in other places) you should report SE or CI. (Note that the correlations in Table 1, which are correlations between blues are not good estimates of genetic correlations).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "For the CV, it is not clear whether you use a leave-genotype-out CV scheme (CV1 in Burgueño et al., Crop Sci, 2010) or one where individual data points are assigned to fold (CV2). These CV schemes represent very different prediction problems and would yield very different results. I suggest you do both.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "I don’t like the plot where you present the average prediction in CV, since the correlations are between BLUES and CV-predictions of them, you should present individual phenotype-predictions, not averages across CV in the plot. Also, it was not clear to me what do you mean by ‘with 10 iterations’ do you mean that you repeated the CV 10 times?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "Many paragraphs begin with a dash, this is likely coming from early drafts, please be sure to review the manuscript carefully before resubmission.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|Human_1|9", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "In general, I think the writing can be improved significantly.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|Human_1|10", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "Try to produce subtlties and titles that are shorter and can be read and understood quickly.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "The notation in table 1 is confusing at least for me, can you replace \"indoor vs field\" in with the actual field number (e.g. 1, 2, 3, 4 ) given in the supplementary table 3?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "Table 1, \"correlation field vs field\", can you use the actual field number?, e.g. 1,2,3,4.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "Figure 1, \"predicted values in a 5-fold cross validation scheme with 10 iterations\", I think is better to write to say that you repeated the cross-validation experiment 10 times as you pointed out in line 598. Another alternative is to write that you performed a simulation experiment with 80% of data in training set and 20% in testing set and that you generated 50 of this partitions at random. This legend appears also in other figures.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "You need to discuss about how the GxE interaction could affect your results.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "For the genomic prediction model (2), why are you including the dominance effects? I assume that the \"genotypic values\" are derived using this model.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "In Figure 4, predicted LAI values from indoors are higher than LAI predicted in the field using UAV. What might be driving this and what could be done to further improve the relationship? The authors might like to comment in the discussion or results section.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|71|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb71", "comment": "Lines 392-405: I agree testing genomic prediction on the recent hybrid varieties is a great thing to do and resembles what might be done in a breeding programme. It might be useful to calculate the genetic variance for the traits within the different groups of hybrids. This is different to the whole genome genetic diversity within the groups (shown in Supp Figure 3). This might reveal that genetic variance for the traits is generally lower in the group of recent hybrid varieties, not just the phenotypic range. Perhaps the authors could create a table summarising genetic variance for each of the traits, in each environment, for each of the groups.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|72|Claude|1", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "The paper's benchmark on real data (HG002) was conducted exclusively within GIAB v0.6 \"high-confidence\" regions, which explicitly exclude challenging genomic regions such as segmental duplications, tandem repeats >10kb, centromeres, and heterochromatin—precisely the regions where SV calling is most difficult and where tool performance differences are most pronounced. This limitation restricts the conclusions that can be drawn about DeBreak's superiority in comprehensive SV detection.\n\n\"The GIAB community genome provided an SV callset of 4,237 deletions and 5,440 insertions from multiple platforms in defined 'high-confidence' regions. Thus, we first benchmarked the SV discovery accuracy in these high-confidence regions.\"\nThe paper acknowledges that benchmarking was performed only in \"high-confidence\" regions. According to the published GIAB v0.6 benchmark paper [[1]](#citation-list), these regions explicitly exclude structural variants in segmental duplications, tandem repeats >10kb, telomeric/centromeric regions, and complex rearrangements. This represents a substantial portion of the genome where SV calling is most challenging and clinically relevant. Recent studies have shown that newer benchmarks like HG002-Q100 v1.1 contain approximately 28,188 SVs compared to 9,705 in v0.6 [[2]](#citation-list), suggesting the v0.6 benchmark significantly underrepresents challenging SVs. The claim that DeBreak provides \"comprehensive and accurate SV discovery\" is therefore not fully supported by benchmarks that systematically exclude the most challenging regions.\n\"Our benchmark also currently does not include more complicated forms of structural variations including inversions, duplications (except for calls annotated as tandem duplications), very large copy number variants (only one deletion and one insertion >100 kb), calls in segmental duplications, calls in tandem repeats >10 kbp, or translocations.\" (From GIAB v0.6 benchmark publication [[1]](#citation-list))\nThis quote from the GIAB v0.6 benchmark paper explicitly states the limitations of the benchmark used in this study. The GIAB v0.6 benchmark does not enable performance assessment for inversion detection or SVs in \"highly repetitive regions like segmental duplications, telomeres, and centromeres that are starting to be resolved by ultralong nanopore reads.\" This means DeBreak's claimed advantages in breakpoint accuracy and comprehensive SV detection remain unvalidated in the regions that are most challenging for alignment-based SV callers.\n\nReferences:\n[1] Zook, J.M. et al. A robust benchmark for detection of germline large deletions and insertions. Nature Biotechnology 38, 1347-1355 (2020). https://www.nature.com/articles/s41587-020-0538-8\n[2] Li, H. et al. Challenges in structural variant calling in low-complexity regions. PMC article (2024). https://pmc.ncbi.nlm.nih.gov/articles/PMC12758381/", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|72|Claude|2", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "The benchmark comparison uses different aligners for different SV calling tools (minimap2 for DeBreak/cuteSV, ngmlr for Sniffles, pbmm2 for pbsv), which confounds the comparison because aligner choice significantly affects SV calling performance. Recent studies demonstrate that the choice of aligner can substantially impact F1 scores for specific SV types, making it difficult to attribute performance differences solely to the SV calling algorithms.\n\n\"DeBreak was applied to minimap2 alignment results with default settings. pbsv was run on pbmm2 alignment results with default settings, and Sniffles was run on the ngmlr alignment results with options '--genotype -s 4/5/6/7/8/9/10'.\"\nThe paper uses three different aligners for four different SV callers. Recent comprehensive benchmarks have demonstrated that aligner choice significantly affects SV calling performance. According to a recent systematic evaluation [[3]](#citation-list), the choice of aligner displayed \"specificity in detecting specific SV types,\" with pbmm2 being more prevalent in top pipelines for deletions and insertions, while NGMLR was most common for inversions, and winnowmap for translocations. This means the observed performance differences may partially reflect aligner effects rather than intrinsic SV caller capabilities. To fairly compare SV callers, the same aligner should ideally be used for all tools, or the aligner-caller combinations should be systematically evaluated.\n\"For INS variant detection, LRA-cuteSV, minimap2-DeBreak, pbmm2-DeBreak, winnowmap-DeBreak, and LRA-DeBreak had higher F1 scores (> 0.94).\" (From Genome Biology 2024 evaluation [[3]](#citation-list))\nThis quote from a comprehensive pipeline evaluation demonstrates that DeBreak performs well with multiple aligners for insertion detection, but other tools show variable performance depending on aligner choice. The same study found that pbmm2 had the highest frequency among top ten combined pipelines regardless of sequencing platform. Since DeBreak was tested with minimap2 while pbsv was tested with pbmm2 (and pbmm2 is often advantageous), this makes direct comparison problematic. The paper's methodology does not control for this known confounding variable.\n\nReferences:\n[3] Ren, J. et al. Comprehensive and deep evaluation of structural variation detection pipelines using long-read sequencing data. Genome Biology (2024). https://link.springer.com/article/10.1186/s13059-024-03324-5", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|72|Claude|3", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "The validation of DeBreak's novel SV calls in the SKBR3 cancer cell line was based on only 15 randomly selected SVs, achieving an 80% validation rate (12/15). This small sample size provides insufficient statistical power to support broad claims about DeBreak's accuracy for cancer genome SV detection, and the paper does not report confidence intervals for this validation rate.\n\n\"To validate potential cancer-related SVs reported only by DeBreak, we designed primers flanking breakpoints for 15 randomly selected SVs (6 deletions, 4 duplications, 3 inversions, and 2 translocations) that spanned more than 10kbp. Polymerase chain reaction (PCR) experiments validated 12 out of 15 DeBreak-novel SVs, with a validation rate of 80%.\"\nThe sample size of 15 SVs is too small to make statistically robust claims about validation rates. Using simple binomial confidence intervals, an 80% success rate (12/15) has a 95% confidence interval of approximately 52%-96%, which is extremely wide. Furthermore, the validation was limited to SVs spanning >10kbp and excluded insertions \"due to length limitations of PCR.\" DeBreak reported 1,333 deletions, 3,073 insertion/duplications, 51 inversions, and 91 translocations that were not previously discovered, but only 15 of these (0.33%) were validated. Standard practice in SV validation studies typically involves larger sample sizes to achieve meaningful precision estimates, often 50+ variants per category [[4]](#citation-list).\n\"Insertions were not validated due to length limitations of PCR.\"\nThis exclusion is notable because insertions represent a substantial portion of DeBreak's novel calls (part of the 3,073 insertion/duplications) and insertions are highlighted in the paper as an area where DeBreak excels. The inability to validate insertions means that claims about DeBreak's superior insertion detection accuracy in cancer genomes remain unvalidated experimentally. This limitation should have been more prominently discussed, as insertion detection is a key claimed advantage of DeBreak.\n\nReferences:\n[4] Sudmant, P.H. et al. An integrated map of structural variation in 2,504 human genomes. Nature 526, 75-81 (2015). https://www.nature.com/articles/nature15394", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|72|Claude|4", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "The simulated benchmark uses pbsim with a fixed error model (accuracy-mean 0.85), which may not capture the full complexity of real sequencing data including context-dependent error patterns, systematic biases, and the complex repeat structures where SV detection is most challenging. This could lead to overestimation of performance differences observed on simulation data compared to real data.\n\n\"Long reads were simulated from the modified genome using pbsim with options '--data-type CLR --model_qc model_qc_clr --depth 25 --accuracy-mean 0.85'.\"\nThe simulation uses a uniform 85% accuracy across all reads, which does not capture the context-dependent error patterns observed in real long-read data, such as elevated error rates in homopolymer regions, GC-biased coverage, and alignment artifacts in repetitive sequences. According to recommendations from comprehensive SV evaluation studies [[5]](#citation-list), \"Most methods perform well on simulated data, which is useful for detecting the theoretical limits of a method or implementation, but is too simple compared to messy real data.\" The paper shows that all tools achieve very high performance on simulated data (Table 1 shows F1 scores >92% for all tools), but performance drops substantially on real data (Table 2), suggesting the simulations may indeed be overly optimistic.\n\"These simulated SVs were assigned as heterozygotes and homozygotes with a ratio of 2:1, and heterozygous SVs were randomly assigned to two haplotypes.\"\nThe simulated SVs were randomly placed across the genome without considering the known non-random distribution of real SVs, which tend to cluster in specific genomic contexts (near transposable elements, in segmental duplications, at specific recombination hotspots). Real SVs also exhibit complex patterns such as nested SVs, overlapping events, and complex rearrangements. The random placement simulation does not test the tools' ability to handle these biologically realistic scenarios. As noted by developers in the field [[5]](#citation-list), \"Claims made about caller performance should be based on actual sequencing data not simulations.\"\n\nReferences:\n[5] Cameron, D.L. et al. Comprehensive evaluation and characterisation of short read general-purpose structural variant calling software. Nature Communications 10, 3240 (2019). https://www.nature.com/articles/s41467-019-11146-4", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|72|GPT|1", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "This paper’s benchmarking methodology is not reproducible and undermines key performance claims because it repeatedly states DeBreak was run with default settings while attributing performance to POA-based breakpoint refinement and local-assembly-based ultra-large insertion rescue, which are optional modules that require explicit flags and a reference genome.\n\n“DeBreak was applied to minimap2 alignment results with default settings.”\nThis sentence appears in the simulation benchmarking protocol and is a central part of how the authors justify the reported accuracy numbers. However, the paper’s headline contributions explicitly depend on optional refinement modules (POA and local assembly), so “default settings” is ambiguous and, in the accompanying code, is not sufficient to activate these modules. Because the manuscript does not state which command-line options were actually used (e.g., whether `--poa` and `--rescue_large_ins` were enabled and whether a reference FASTA was provided), an independent reader cannot reproduce the reported breakpoint refinement and large-insertion behavior. This is not a minor reporting omission: it directly affects whether DeBreak is being evaluated as the method described in the abstract versus a reduced feature set. In SV benchmarking, small differences in enabled modules can materially change both recall (e.g., rescued insertions) and breakpoint accuracy (e.g., consensus refinement). As written, the benchmark description is internally inconsistent with the claimed sources of performance improvements.\n“Notably, for ultra-large insertions longer than the sequencing reads (>10kbp), DeBreak achieved higher accuracy, recall, and precision than the other three SV callers (Fig S7), benefiting from its large-insertion detection module with local de novo assembly.”\nThis sentence attributes improved performance on ultra-large insertions specifically to a dedicated local assembly module, implying that module was enabled during benchmarking. Yet the Methods section does not describe enabling any insertion-rescue option, nor does it document providing the required reference genome input. If the module was not enabled, then the stated causal mechanism for improved ultra-large insertion performance is unsupported by the experimental configuration. If the module was enabled, then the absence of the exact commands and flags prevents reproduction and proper peer assessment of fairness (e.g., which aligner/reference was used for contig alignment). In either case, the paper’s conclusion that DeBreak outperforms other tools for very long insertions is not methodologically well-grounded from the information provided. This problem is magnified because ultra-large insertions are precisely where callers’ behaviors diverge depending on assembly/refinement choices. The result is that a key claimed advantage cannot be independently verified from the manuscript as written.\n```python\nparser.add_argument('--rescue_large_ins',action='store_true',default=False,help='rescue large INS. wtdbg2,minimap2,ref required')\nparser.add_argument('--poa',action='store_true',default=False,help='POA for accurate breakpoint. wtdbg2,minimap2,ref required.')\nparser.add_argument('-r','--ref',type=str,default=False,help='reference genome. Should be same with SAM/BAM')\n```\nThis code block from the provided DeBreak v1.0.2 entry script shows that both POA breakpoint refinement and large-insertion rescue are optional modules that are off by default (`default=False`). It also explicitly encodes that these modules require a reference genome (`ref required`) and additional external tools, contradicting any implication that they are automatically exercised under an unspecified “default” benchmark configuration. Therefore, the manuscript’s repeated statement that DeBreak was run “with default settings” is not sufficient to infer that the evaluated pipeline included the paper’s main proposed components. In methods-focused computational genomics papers, core pipeline toggles must be reported as exact flags to make results reproducible and interpretable. Because these flags directly change which algorithmic steps run, missing them can materially change both recall (e.g., rescued large insertions) and breakpoint precision. The code thus demonstrates that the manuscript’s benchmark description does not uniquely define the evaluated method.\n```python\n# POA for all SVs\nif debreak_args.poa:\n\tlogfile=open(writepath+'log.txt','a')\n\n\tif not debreak_args.ref:\n\t\tlogfile.write('Warning: No reference genome provided. Abort breakpoint refinement.\\n')\n\t\tlogfile.close()\n```\nThis snippet shows that even when the POA module is explicitly requested (`if debreak_args.poa:`), breakpoint refinement is immediately aborted when no reference genome is provided. That behavior directly affects the manuscript’s central claim of improved breakpoint accuracy from POA, because it cannot occur unless both `--poa` and `--ref` are supplied. The Methods text does not state that a reference FASTA was provided in the key benchmarks (it repeatedly says “default settings”), so readers cannot verify that POA refinement was actually executed. If POA was not executed, then any reported breakpoint improvements cannot be attributed to the described consensus-refinement mechanism. If it was executed, then the manuscript’s lack of explicit commands prevents reproduction and independent assessment of the results. Either way, this code makes the benchmark reporting gap a substantive methodological problem, not a documentation nit.\n```sh\n# quick SV calling with sorted bam\ndebreak --bam merged.sort.bam --outpath debreak_out/\n\n# Accurate SV calling with sorted bam (reference genome needed)\ndebreak --bam merged.sort.bam --outpath debreak_out/ --rescue_large_ins --rescue_dup --poa --ref hg38.fa \n```\nThe project’s own README explicitly distinguishes a “quick” default run from an “Accurate” run that enables POA and insertion/duplication rescue and requires a reference genome. This directly contradicts the manuscript’s implication that default settings suffice for the reported “single base-pair resolution” refinement and ultra-large insertion reconstruction. Because the paper’s results and discussion attribute improvements to these modules, the benchmark should specify whether the “Accurate” configuration was used and under what exact command lines. Without that, readers cannot reproduce the headline results nor assess whether comparisons to other callers were performed with analogous feature sets. In computational genomics, such configuration differences are a major source of irreproducibility and can change measured precision/recall substantially. The README therefore serves as concrete evidence that “default settings” does not uniquely define the evaluated method. This is a substantial methodology-reporting gap for a methods-focused manuscript.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|72|GPT|3", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "This paper’s genotyping comparison is methodologically unreliable because it defines “genotyping accuracy” as correct genotypes divided by the total number of SVs reported by each caller, conflating genotyping correctness with each tool’s sensitivity/number of calls and potentially biasing conclusions in Table S1.\n\n“We also benchmarked genotyping accuracy of the four tested SV callers with the high-confidence SV callset. On the three datasets, DeBreak and cuteSV performed better than pbsv and Sniffles (Table S1).”\nThis sentence claims a comparative genotyping advantage for DeBreak, implying that the metric isolates genotype inference quality. However, the GIAB benchmark is used as the reference, and callers can differ substantially in which variants they report (especially across depths and platforms), so a genotyping metric must control for detection differences to be comparable. If a method reports fewer variants (e.g., only the easiest ones), its “genotyping accuracy” can appear inflated even if its genotype assignments are not better on matched true positives. The manuscript does not state whether genotyping was assessed on matched true positives (shared variant matches) versus all reported variants, which is critical for interpretation. Because genotyping and discovery are different tasks, conflating them can produce misleading rankings across callers. The supplementary definition (below) shows that the paper indeed conflates these, which undermines the reliability of the conclusion quoted here. Therefore, the paper’s stated genotyping superiority is not robustly supported by a standard, comparable evaluation design.\n“The genotyping accuracy is calculated as the number of SVs with the correct genotype divided by the total number of SVs reported by each SV caller.”\nThis definition makes the denominator caller-dependent, meaning the metric is not directly comparable across tools with different sensitivity and filtering behavior. In particular, the metric mixes (i) whether a caller discovered a variant at all and (ii) whether, conditional on discovery, the genotype was correct. A caller that outputs a smaller, higher-confidence subset can score higher even if its genotype inference is weaker on challenging variants, while a more sensitive caller can be penalized for including harder-to-genotype calls. Standard practice in benchmark-based genotyping evaluation is to compute genotype concordance among matched true positives (or among the benchmark set after matching), precisely to avoid confounding by callset size. The paper’s definition instead resembles “genotype precision among reported calls,” not “genotype accuracy” in a benchmarking sense. This matters because the manuscript uses the metric to claim cross-platform genotyping advantages, which requires a controlled comparison. As a result, the genotyping conclusions drawn from Table S1 are potentially biased and should be reconsidered using a matched-TP genotype concordance evaluation.\n“Among the TP calls, genotype matched rates of DELLY are from 90.1 to 92.1% and of pbsv are from 73.9 to 90.5% (78.3–91.2% for SV ≥ 30bp).” [[3]](#ref3)\nThis passage exemplifies a common benchmarking approach: genotype matching is reported conditional on calls being true positives, which keeps the denominator comparable across methods and separates detection from genotyping. In contrast, the manuscript under review divides by “the total number of SVs reported,” which couples the genotyping metric to a method’s call rate and filtering strategy. The external quote makes explicit that genotype evaluation can and should be restricted to TP calls (after matching), which yields a clearer interpretation of genotyping quality. Because the reviewed paper does not adopt this conditional evaluation, its reported “genotyping accuracy” can change simply by altering detection thresholds rather than improving genotype inference. This can lead to incorrect tool rankings, especially across platforms where the number of reported SVs differs substantially. Therefore, the paper’s metric choice is not aligned with established benchmarking practice and weakens the genotyping conclusions.\n“These metrics are SVTYPE matching, reference distance, reciprocal overlap, size similarity, sequence similarity, and genotype matching.” [[4]](#ref4)\nThis sentence describes genotype matching as one component of SV comparison in benchmarking tools, reinforcing that genotyping assessment is typically embedded in a matching framework that first establishes which variants correspond across callsets. That matching step is essential because genotype correctness is only meaningful for comparable variant representations (i.e., the same SV event). The manuscript’s Table S1 definition does not indicate any such matching restriction and instead normalizes by total reported calls, which is sensitive to representation and filtering differences. In practice, genotype matching is usually computed for matched variants that meet defined similarity thresholds, precisely to avoid treating unmatched calls (which may be FPs or simply unrepresented in the other callset) as part of the genotype denominator. The external quote therefore highlights the methodological gap: the reviewed paper uses a genotyping metric without a comparable matched-variant basis. As a result, the “genotyping accuracy” values in Table S1 are difficult to interpret as a measure of genotype inference quality. This reduces confidence in the paper’s claims about DeBreak’s genotyping performance relative to other callers.\n\nReferences:\n[3] [Yang & Chaisson, “TT-Mars: structural variants assessment based on haplotype-resolved assemblies,” Genome Biology (2022)](https://pmc.ncbi.nlm.nih.gov/articles/PMC9077962/)\n[4] [English et al., “Truvari: refined structural variant comparison preserves allelic diversity,” Genome Biology (2022)](https://pmc.ncbi.nlm.nih.gov/articles/PMC9793516/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|72|GPT|4", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "This paper’s broad conclusions about comprehensive SV discovery and superiority on real data are not adequately supported because the main real-human benchmark (GIAB HG002 Tier1 v0.6) evaluates only insertions and deletions, leaving duplications, inversions, translocations, and complex SV performance largely unvalidated on real truth sets.\n\n“Based on alignment results, DeBreak employs a density-based approach for clustering SV candidates together with a local de novo assembly approach for reconstructing long insertions. A partial order alignment algorithm ensures precise SV breakpoints with single base-pair resolution, and a k-means clustering method can report multi-allelic SV events. DeBreak outperforms existing tools on both simulated and real long-read sequencing data from both PacBio and Nanopore platforms.”\nThese abstract-level statements collectively claim comprehensive capability (beyond DEL/INS) and superiority on real datasets across platforms. For such a claim to be robust, real-data benchmarks should cover multiple SV classes (e.g., INV, DUP, TRA) using credible truth sets or orthogonal validation, not only simulations. Yet the paper’s primary real-sample benchmarking relies on a GIAB SV callset that the manuscript itself describes as deletions and insertions, leaving other SV types without comparable real truth evaluation. The cancer cell line section provides some PCR validation but only for 15 randomly selected large SVs and explicitly excludes insertions from validation, which does not establish comprehensive performance. As a result, the abstract’s general “outperforms” claim is broader than what the provided real-data evidence directly supports. In SV calling, performance can vary dramatically by SV class, size, and genomic context, so extrapolating from DEL/INS benchmarking to all SV types is not justified without additional validation. Therefore, the paper’s overarching conclusions overreach the demonstrated evaluation scope.\n“The GIAB community genome provided an SV callset of 4,237 deletions and 5,440 insertions from multiple platforms in defined “high-confidence” regions34. Thus, we first benchmarked the SV discovery accuracy in these high-confidence regions.”\nThis sentence makes explicit that the key real-genome benchmark truth set used for accuracy evaluation consists of deletions and insertions in high-confidence regions. Consequently, the reported recall/precision/F1 comparisons on HG002 do not directly evaluate duplications, inversions, translocations, or complex SV classes on real truth data. However, the manuscript later generalizes its conclusions to “different types of SVs” and emphasizes “comprehensive” SV discovery in the abstract and discussion. While simulations can provide some evidence for additional SV types, simulations often lack the alignment ambiguities and genomic complexities (e.g., repeats, segmental duplications) that dominate real-world calling errors. The paper does not present a comparable real-sample benchmark for INV/DUP/TRA with a validated truth set, so readers cannot assess whether performance generalizes beyond DEL/INS. This is a significant limitation because callers frequently exhibit class-specific tradeoffs and different breakpoint behaviors in real data. Therefore, the paper’s real-data benchmarking scope is narrower than its stated comprehensive conclusions.\n“The final benchmark set contains 12745 isolated, sequence-resolved insertion and deletion calls ≥50 base pairs (bp) discovered by at least 2 technologies or 5 callsets, genotyped as heterozygous or homozygous variants by long reads.” [[1]](#ref1)\nThis external description of the GIAB SV benchmark clarifies that the benchmark is fundamentally centered on insertions and deletions, aligning with what the manuscript uses for HG002 evaluation. Therefore, benchmarking on GIAB v0.6 Tier1 cannot by itself validate claims about caller accuracy for other SV types such as inversions, duplications, and translocations on real genomes. The reviewed paper nonetheless presents DeBreak as comprehensive and implies superiority across SV categories and applications (including cancer rearrangements), which would require additional truth sets or validation strategies for those other SV types. The GIAB benchmark’s focus on DEL/INS also means that reported gains in F1 on HG002 primarily reflect those classes, limiting the generality of conclusions. In addition, the benchmark’s “isolated” calls do not fully represent clustered or complex rearrangements, which are central to the paper’s cancer motivation. Thus, the external benchmark scope reinforces that the manuscript’s real-data evaluation does not substantiate all of its broad claims.\n“Since the GIAB benchmark set only contains deletions and insertions, validation of other types of SVs are not included.” [[3]](#ref3)\nThis statement from an SV benchmarking/validation paper underscores the exact limitation faced by the reviewed manuscript’s HG002 evaluation: GIAB v0.6 does not validate non-DEL/INS SV types. The reviewed paper uses the GIAB set to support a broad “comprehensive and accurate” narrative, but this external quote makes clear that such a benchmark cannot assess accuracy for inversions, duplications, and other rearrangements. Without alternative benchmark resources (e.g., assembly-content validation, curated sets for inversions, or orthogonal assays), claims about these SV types remain largely untested on real ground truth. The manuscript’s limited PCR validation in SKBR3, while helpful, is small-scale and selective (e.g., excluding insertions) and does not replace systematic truth-based evaluation. Therefore, the external evidence supports that the paper’s comprehensive SV performance claims are not fully validated by its chosen benchmark. This is a substantive conclusions-robustness issue rather than a minor scope caveat.\n\nReferences:\n[1] [Zook et al., “A robust benchmark for germline structural variant detection,” bioRxiv (v1, 2019), 10.1101/664623](https://www.biorxiv.org/content/10.1101/664623v1)\n[3] [Yang & Chaisson, “TT-Mars: structural variants assessment based on haplotype-resolved assemblies,” Genome Biology (2022)](https://pmc.ncbi.nlm.nih.gov/articles/PMC9077962/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|72|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "The benchmarking methodology uses different aligners for different structural variant callers (minimap2 for DeBreak and cuteSV, ngmlr for Sniffles), which introduces a confounding variable and makes the comparison unfair.\n\n\"DeBreak and cuteSV were applied to minimap2 alignment with default settings. pbsv was applied to pbmm2 alignment with default settings. Sniffles was applied to ngmlr alignment with option “--genotype -s 9/9/12”...\"\nThe use of `minimap2` for DeBreak and `cuteSV` while using `ngmlr` for Sniffles makes it difficult to attribute performance differences solely to the SV callers. `minimap2` and `ngmlr` have different alignment characteristics and error profiles [2]. A fair comparison would require running all tools on alignments generated by the same aligner (or both aligners for all tools) to disentangle the effect of the aligner from the SV caller's performance.\n\"Considering that different aligners could affect the performance of read alignment-based SV callers...\" [3]\nOther benchmarking studies explicitly acknowledge the impact of aligners and control for it by testing combinations of aligners and callers. The failure to do so in this paper weakens the validity of the claim that DeBreak is superior to Sniffles, as the difference could be partly due to the aligner used.\n\nReferences:\n[2] [Comparison of long-read aligners](https://www.nature.com/articles/s41598-024-56604-2)\n[3] [Tradeoffs in alignment and assembly-based methods for structural variant detection with long-read sequencing](https://www.nature.com/articles/s41467-024-46614-z)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|72|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "The paper fails to compare DeBreak with other relevant and widely used structural variant callers available at the time of writing, such as SVIM and NanoVar, limiting the comprehensiveness of the evaluation.\n\n\"To benchmark the performance of SV discovery, we first compared DeBreak with three SV callers, Sniffles, pbsv, and cuteSV...\"\nThe authors only compare against Sniffles, pbsv, and cuteSV. However, other tools like SVIM [4] and NanoVar [5] were published and available before this preprint (2019 and 2020, respectively) and are commonly included in such benchmarks. Excluding these tools means the paper does not demonstrate DeBreak's performance relative to the full landscape of existing solutions.\n\"SVIM: structural variant identification using mapped long reads\" [4]\nSVIM is a significant tool in the field that uses a different approach (clustering of signatures) and is often cited as a strong performer in benchmarks. Its omission leaves a gap in the evaluation of DeBreak's relative merit.\n\nReferences:\n[4] [SVIM: structural variant identification using mapped long reads](https://academic.oup.com/bioinformatics/article/35/17/2907/5304363)\n[5] [NanoVar: accurate characterization of patients’ genomic structural variants using low-depth nanopore sequencing](https://genomebiology.biomedcentral.com/articles/10.1186/s13059-020-02003-x)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|72|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "Please make DeBreak support python3. Python2 has retired for more than a year. Users would question the long-term commitment to DeBreak if they see it support python2 only. Python2-only also makes it difficult for others to contribute to DeBreak as there will be fewer Python2 programmers in future.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|72|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "It would be good to stratify the result by repeat classes. For example, what is the accuracy for ALUs, LINE1s, SVAs, STRs, VNTRs and non-repeats? I predict that the accuracy of every caller will be near perfect for ALUs and LINE1s and will drop a lot in VNTRs. It is rare to see such stratification in SV caller papers, but I think this is an important analysis and is likely to benefit this manuscript. The authors can run RepeatMasker/TRF on the longest allele to annotate repeats.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|72|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "1. I am a little concerned with the low consistency between DeBreak and PAV. Could the authors compare PAV HG002 calls to GIAB? It would be important to understand the accuracy of PAV. Another option is to use dipcall for assembly-based SV calling. Dipcall is known to agree with GIAB well. Its accuracy is lower than read-based SV calls mostly due to different variant representations. Note that dipcall also generates confident regions like GIAB.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|72|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "Does DeBreak assemble all reads mapped to a candidate SV, or only assemble reads that contains the SV?", "reviewer_type": "human", "label": "error", "error_type": "Neglect", "label_origin": "expert+llm-filter"}
{"id": "prb|72|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "Installation 1: I do have several comments about the code and its implementation that have been challenging. Firstly, the code is written in python 2.7 - now end of life (not supported). Really the tool should be updated to a current version of python. Similarly, the dependencies required for installing are old with all having been updated in the last two years versus the tested versions described.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|72|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "Installation 2: We also could not get the code to install using the suggested conda instructions - instead we had to install in a specific environment file (see below for the yaml file we created to make an environment). This may have been a peculiarity of our system but conda was unable to resolve the dependencies when creating an environment in the stepwise manner presented by the authors.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|72|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "Incorrectly formatted VCF: The biggest concern was that we could not parse the VCF output using conventional tools such as bedtools intersect. The records as written are identified as being invalid.\n\nUsing the vcf_validator tool ( from EBI) we see the following report for an example VCF file generated by DeBreak:\n\n\"According to the VCF specification, the input file is not valid\nError: INFO MAPQ does not match the meta specification Type=Integer (not in integer format). This occurs 795 time(s), first time in line 23.\nWarning: A valid 'reference' entry is not listed in the meta section. This occurs 1 time(s), first time in line 23.\"\n\nTo understand this better, we did investigate the code. Overall the code is poorly documented and relies heavily on manual execution of tasks including compiling commands to run using os.system as well as manual writing of VCF files - the authors should consider using a library such as pysam to handle these functions to ensure compatibility. Essentially, the code could be significantly improved for both readability and speed. This is not essential for publication but it will be important for those seeking to use the tool in the future.\n\nEnsuring the VCF file is the correct format is essential.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|72|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "Tool versioning: With respect to the manuscript itself, I found the text clear and easy to interpret. The authors should specify the benchmark software versions used for cuteSV, sniffles etc. This is particularly important as sniffles has recently been updated to version 2 and I assume the work presented here is with respect to an earlier version. Similarly cuteSV has been updated many times since its publication. For the record, neither cuteSV (1.0.13) or Sniffles (vs2) could detect the known breakpoint in our sample- which was detected by DeBreak.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|72|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "Table Details: In Table S1 (genotyping accuracy), the authors show poorer performance for debreak in PacBIO HiFi reads than CLR. This is surprising - every other tool improves its performance as the read quality improves. The authors do not comment on this but it is very interesting - do they have an explanation for why this might be? Is DeBreak somehow optimised for noisier reads? This also contrasts with the F1 scores presented in table S2 - where HiFi does result in improved performance.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|72|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "[Abstract] a) The last sentence \"DeBreak also demonstrates excellent performance in supplementing whole-genome assembly methods.\" should be toned down - it is unclear based on the presented results whether the DeBreak-unique calls (compared to assembly-based methods) are true- or false-positive calls.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|72|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "[Simulations] Simulations:\n\na) Simulations are always a good starting point, but the simulation approach chosen by the authors is simplistic. Structural variants tend to emerge around areas of existing sequence homology, i.e. not randomly, but in more repeat-rich / difficult-to-analyze regions of the human genome. An improved or second simulation experiment could be constructed e.g. by varying the copy number of existing repeats in the human genome. Alternatively, the simulations part could be left as it is, but its limitations would have to be made more clear in the section describing the results and in the Discussion.\n\nb) In the reduced coverage simulations part of the results, it would be important to assess the effect of coverage on SV breakpoint detection accuracy.\n\nc) DeBreak includes a specific component for the detection of long insertions. It would be important to better understand the specific contribution of this component to the algorithm's overall ability to detect insertions of different lengths (i.e., conditional on insertion length). Also, the paper includes a real-data evaluation of DeBreak's performance on insertions conditional on insertion length(see Figure 2); but even in the 50kb bin, DeBreak still achieves an F1 score of about 0.75. It would be important to better understand from which insertion size onwards the performance of DeBreak really starts breaking down; this could be assessed using simulations.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|72|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "[HG002 results]\n\na) The authors highlight the importance of multi-allelic copy number variations (line 139) - what exactly is meant by \"multi-allelic\" here? Multi-allelic in one genome or in the human population? Also, if truth data are available multi-allelic copy number variants in HG002, it would be important to measure the accuracy of DeBreak's multi-allelic calls against these (genotype accuracy and breakpoint accuracy).\n\nb) Downsampling: these results are very relevant; it would be important, however, to also understand the effect of reduced coverage on breakpoint detection accuracy.\n\nc) Line 174: \"Taken together, these results highlight that DeBreak can accurately identify different types of SVs with precise breakpoints in real human genomes.\". This statement should be explicitly limited to insertions and deletions (which are the types of SV calls that were validated here).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|72|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "[HGSVC results]\n\na) It would be important to also specify and discuss recall and precision of the different SV detection methods (Table S2 only specifies F1 scores). An additional table with these metrics could be added in which all evaluated samples (of one sequencing technology type) are combined.\n\nb) Why was Sniffles not applied to these samples?\n\nc) Why is no evaluation of SV genotype accuracy carried out on this dataset?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|72|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "[Discussion]\n\na) It would be good to include a brief section on the effect of the sequencing read data type (CLR, HiFi, Nanopore) on accuracy.\n\nb) While DeBreak can call insertions, deletions, inversions, and translocations, the empirical validation focuses on insertions and deletions (due to the availability of truth SV data). A brief paragraph discussing this and highlighting the fact that additional empirical validation of the algorithm's performance on inversions and translocations would be desirable should be added to the Discussion.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|72|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "[Methods]\n\na) Overall the Methods section is too vague and not specific enough.\n\nb) Raw SV signal detection: Please be more specific about how exactly \"raw SV signals\" are detected based on the alignments. Please provide details on the density-based clustering of SV signals.\n\nc) It is unclear to us what happens to translocations during the SV detection and clustering phase; in particular, it is unclear to us how translocations between different chromosomes are detected / handled (as chromosomes are processed independently).\n\nd) Large insertion detection via local assembly: How exactly is \"enriched clipped alignment\" defined? It is not clear to us how this step differs from the main raw SV signal detection step - which is also followed by a POA-based reassembly step? Also, it would seem to us that one key problem with long insertions is that the insertion may be longer than the read length - if we understand the approach of DeBreak correctly, however, the local re-assembly will only include reads that extend into the areas outside of the insertion (and thus miss the \"middle region\" of long insertions)? Last, but not least, how exactly is the local de novo assembly step carried out (e.g. using an external long-read assembly algorithm)?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|72|Human_3|7", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "[General points]a) PBHoney was mentioned in the introduction but is not evaluated - could the authors explicitly comment on why this is (or alternatively add it to the evaluations)?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|72|Human_3|8", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "[Simulations]\n\na) There are 3 simulated datasets with varying read lengths, but Table 1 lumps them together - it would be good to see results broken down by read length (e.g. in the Supplement) to better understand potential impacts of read length. How exactly were translocations modeled (inter-chromosomal or across chromosomes)?\n\nb) Adding a brief explanation where the different SV length simulation peaks in Figure S1 come from to the figure's legend would be helpful.\n\nc) Figure S3b seems to show a systematic bias with respect to the breakpoint accuracy of DeBreak-determined duplications - could the authors comment on that?\n\nd) Also, the red bars in Figure S3b are kind of hard to identify (apart from the outliers, see previous point) - consider modifying the graph to enable a better distinction between the variant types?\n\ne) The simulations could be extended by a simulated Nanopore dataset; or a discussion point could be added explaining why the results of a Nanopore simulation would be expected to be similar to the PacBio simulation results.\n\nf) Line 118, \"81.33% of SVs with ±1bp shift around the SV breakpoint\": This statistic include correctly determind (= 0bp shift) breakpoints, correct? Phrasing this as \"within 1bp of the true SV breakpoint\" may be more clear.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|72|Human_3|9", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "[HG002 results]\n\na) It is not exactly clear to us how genotype accuracy is calculated here. What are the possible \"genotypes\" in the truth set - just 0, 1 or 2, or does the truth also include copy-number-variant genotypes? Also, is genotyping accuracy calculated on the respective algorithm's call set, or on the complete call set (both ways to evaluate genotyping accuracy are important and should be included).\n\nb) Please also specify +-1bp breakpoint accuracy for all algorithms in the text (to make results fully comparable to the simulation experiment).\n\nc) Figure 2: Please make the utilized read data type (CLR, HiFi, Nanopore) more explicit in the figure and the legend.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|72|Human_3|10", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "[HGSVC results]\n\na) Please also specify +-1bp breakpoint accuracy for all algorithms in the text (to make results fully comparable to the simulation experiment), and specify breakpoint accuracy as % of calls made\n\nb) It would be interesting (though not essential) to see results for multi-allelic copy number variations here as well.\n\nc) Line 207, \"suggesting that alignment-based SV callers identified SV calls more consistently.\": More consistently than assembly-based methods? As only one assembly-based data source (PAV) is considered here, this claim does not seem to follow.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|72|Human_3|11", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "[Cancer genome results]\n\na) A brief description of the input data (technology type, coverage, read lengths) in the main text would be very helpful.\n\nb) Would it be possible to construct an assembly-based \"truth set\" here as well?\n\nc) The fusion gene-specific validation approach leveraging IsoSeq data is very interesting. Could the same approach be applied to the results of the other SV calling methods (to the extent that they are capable of calling translocations) as well? (We would view this as very interesting, though not essential)", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|72|Human_3|12", "source": "prb", "split": "test", "paper_id": "prb72", "comment": "Methods:\n\na) Explicitly mentioning the multi-allele step of the workflow may be helpful.\n\nb) Line 312: \"The density of SV raw signal is computed for each position on the chromosome (Supp fig)\" -> Figure number missing.\n\nc) Section 3.33 only mentions the PacBio CLR dataset, omitting the Nanopore and HiFi datasets (which are also downsampled).\n\nd) Line 342: Please define when exactly a read is counted as \"supporting\"", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|73|Claude|1", "source": "prb", "split": "test", "paper_id": "prb73", "comment": "The paper identifies rs8191642[G], a synonymous variant in NEIL2, as associated with increased paternally transmitted mDNMs but provides no mechanistic evidence explaining how a synonymous (silent) variant could affect microsatellite mutation rates. This represents a significant gap in supporting the paper's major conclusion that genetic variants affect microsatellite mutation rates.\n\n\"Furthermore, we find a novel association between mDNM counts without homopolymers and two correlated (r²=0.988) SNPs, rs8191642 (P =5.6 · 10⁻¹⁰) a synonymous variant (Pro188), and rs8191649 (1.4 · 10⁻⁹), an intronic variant, both in NEIL2, a glycolase involved in both transcription and replication associated base excision repair of DNA damaged by oxidation or by mutagenic agents.\"\nThe paper identifies a synonymous variant as the lead marker for the NEIL2 association but fails to provide any mechanistic explanation for how a synonymous (codon-changing but not amino acid-changing) variant could affect NEIL2 protein function or microsatellite mutation rates. Synonymous variants by definition do not alter protein sequence, yet the paper draws strong conclusions about this variant's role without addressing this fundamental question of how the variant exerts its effect.\n\"NEIL2 has been reported to function in both transcription and replication coupled repair and thus, it is likely that the association between the synonymous variant in NEIL2 and the number of paternally transmitted mDNMs is due to the more frequent replication of spermatogonia.\"\nThis explanation addresses why the effect is paternal-specific but does not explain the mechanism by which a synonymous variant affects NEIL2 function. While synonymous variants can affect gene expression through codon usage, mRNA stability, or splicing, the paper provides no evidence for any such mechanism. The published literature on NEIL2 functional variants typically focuses on missense or regulatory variants, not synonymous changes at Pro188 [[1]](#citation-1).\n* Quote from the literature: \"Synonymous sites are generally considered to be functionally neutral. However, there are recent contradictory findings suggesting that synonymous alleles might have functional roles in various molecular aspects\" [[2]](#citation-2).\nWhile synonymous variants can occasionally have functional effects through mechanisms such as altered codon usage, mRNA secondary structure, or splicing effects, the paper does not investigate any of these potential mechanisms for rs8191642. A comprehensive analysis should include eQTL data to determine if the variant affects NEIL2 expression levels, or other functional validation to support the biological plausibility of the association. Without such evidence, the causal relationship between this synonymous variant and mDNM rate remains speculative.\n\nReferences:\n[1] [DNA glycosylase NEIL2 functions in multiple cellular processes](https://pmc.ncbi.nlm.nih.gov/articles/PMC10277195/) - Chakraborty A, et al. Frontiers in Cell and Developmental Biology, 2023.\n[2] [Synonymous Codon Usage Controls Various Molecular Aspects](https://pmc.ncbi.nlm.nih.gov/articles/PMC5769864/) - Shabalina SA, et al. PLoS Biology, 2017.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|73|Claude|2", "source": "prb", "split": "test", "paper_id": "prb73", "comment": "The GWAS identifying mutator variants was conducted exclusively in an Icelandic population, which has known founder effects and reduced genetic diversity. The identified associations with rs4987188 (MSH2) and rs8191642 (NEIL2) were not replicated in the UK Biobank cohort, limiting the generalizability of these findings to other populations.\n\n\"Using 6,084 Icelandic parent-offspring trios we estimate 63.7 (95% CI: 61.9-65.4) microsatellite de novo mutations (mDNMs) per offspring per generation.\"\nAll mDNM analysis was conducted in Icelandic trios. While Iceland provides advantages such as detailed genealogical records and homogeneous population structure that facilitate genetic studies, the founder effect and genetic drift in Iceland may have elevated the frequencies of certain variants that are rare or have different effects in other populations. The allele frequency of rs4987188[A] at 1.9% and rs8191642[G] at 20.3% may differ substantially in non-European or non-Icelandic populations.\n\"We used popSTR to call genotypes at 5,401,401 autosomal short tandem repeats (STRs) in two large WGS datasets, 53,026 Icelanders and 150,119 participants in the UKB\"\nAlthough the UK Biobank data was used for microsatellite polymorphism analysis, the GWAS for mutator variants was not replicated in this independent cohort. A robust genetic finding should ideally be validated in multiple populations to ensure the associations are not population-specific artifacts.\n* Quote from the literature: \"Icelandic genetic studies have been powerful due to the detailed genealogical records... but the relatively small founder population size and genetic drift mean that some variants may have unusually high frequencies compared to other populations\" [[3]](#citation-3).\nPopulation-specific genetic architecture can lead to associations that do not replicate across populations. For a finding as significant as identifying human germline mutator alleles, replication in an independent and genetically diverse cohort would substantially strengthen the conclusions. The paper notes that microsatellite genotypes for UKB are \"publicly available,\" suggesting the data for potential replication exists but was not utilized for the GWAS validation.\n\nReferences:\n[3] [Large-scale whole-genome sequencing of the Icelandic population](https://www.nature.com/articles/ng.3247) - Gudbjartsson DF, et al. Nature Genetics, 2015.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|73|Claude|3", "source": "prb", "split": "test", "paper_id": "prb73", "comment": "The validation analyses reveal an 11.3% error rate for homopolymer mDNMs (compared to 5-6% for other repeat types), yet homopolymers are included in the genome-wide mDNM rate estimate of 63.7 per generation. This inflates the estimated mutation rate and may bias conclusions about mutation patterns.\n\n\"Not surprisingly, homopolymers had the lowest validation rate for both mDNMs shared by monozygotic twins (88.7%, Supplementary Table 8)\"\nAn 88.7% validation rate corresponds to an 11.3% false positive rate for homopolymer mDNMs, which is approximately double the false positive rate of other mDNM categories. Despite this substantially higher error rate, homopolymers contribute significantly to the total mDNM count (Table S30 shows 8,103 homopolymer mDNMs out of 46,239 phased mDNMs, approximately 17.5%).\n\"We estimated the false positive rate of our method between 2.0-5.6% using three approaches; PacBio CCS sequence data, mDNM sharing between monozygotic twins and haplotype sharing across three-generation families\"\nThe stated overall false positive rate range obscures the heterogeneity between motif lengths. The 2.0-5.6% range appears to reflect non-homopolymer repeats, while homopolymers have a distinctly higher error rate. When reporting genome-wide estimates that include homopolymers, the uncertainty should be appropriately weighted to reflect this differential error rate.\n\"Homopolymer mDNMs have a higher false positive rate than other mDNM categories. To assess the robustness of our results, we reran the GWAS on mDNM counts per parent without mDNMs occurring at homopolymers.\"\nWhile the authors appropriately exclude homopolymers in sensitivity analyses for the GWAS, the primary genome-wide mDNM rate estimate of 63.7 per generation still includes homopolymers. The paper also reports an estimate excluding homopolymers (48.2 mDNMs per generation), but this is presented as secondary. Given the known higher error rates at homopolymers in short-read sequencing data [[4]](#citation-4), the estimate excluding homopolymers may be more reliable and should be given equal prominence.\n\nReferences:\n[4] [A direct characterization of human mutation based on microsatellites](https://www.nature.com/articles/ng.2398) - Sun JX, et al. Nature Genetics, 2012.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|73|Claude|4", "source": "prb", "split": "test", "paper_id": "prb73", "comment": "The paper reports that rs4987188[A] (p.Gly322Asp) in MSH2 significantly increases mDNM rates but shows no association with colorectal or endometrial cancer risk. This creates a paradox given that MSH2 is one of the primary genes causing Lynch syndrome through mismatch repair deficiency, which is characterized by microsatellite instability. The paper does not adequately reconcile this discrepancy or discuss why a variant that increases germline microsatellite mutations would not also increase cancer risk.\n\n\"Multiple variants in MSH2 have been reported to cause Lynch syndrome (also known as hereditary non-polyposis colorectal cancer, HNPCC), which results in increased risk of endometrial, colorectal and other cancers. We tested rs4987188[A] for association with an increased risk of endometrial and colorectal cancer in both the Icelandic and combined meta-analysis data sets available at deCODE genetics, but found no such association.\"\nThe paper acknowledges testing for cancer associations and finding none, but does not adequately discuss why this might be. Lynch syndrome results from mismatch repair deficiency leading to somatic microsatellite instability (MSI), which drives tumorigenesis. If rs4987188[A] increases germline microsatellite mutation rates by impairing mismatch repair, it would be expected to also increase MSI in somatic tissues and thus cancer risk.\n\"Functional studies of the yeast homologue of rs4987188 indicate that it results in a modest decrease in mismatch repair efficiency.\"\nThe paper cites evidence that this variant causes modest MMR impairment in yeast, yet concludes it does not increase cancer risk in humans. This creates an apparent contradiction that deserves more discussion. One possibility is that the variant is a hypomorphic allele with sufficient residual function to prevent somatic MSI but with detectable effects on germline mutation rates, but this hypothesis is not explicitly stated or tested.\n* Quote from ClinVar: \"NM_000251.3(MSH2):c.965G>A (p.Gly322Asp) - Benign/Likely benign\" [[5]](#citation-5).\nWhile the ClinVar classification as benign/likely benign for Lynch syndrome is consistent with the paper's finding of no cancer association, it raises questions about whether this variant truly has a biologically meaningful effect on mismatch repair. The paper should more thoroughly discuss how a variant classified as benign for disease can nonetheless have a significant effect on germline mutation rates, or whether the GWAS association might reflect linkage disequilibrium with another causal variant.\n\nReferences:\n[5] [ClinVar: NM_000251.3(MSH2):c.965G>A (p.Gly322Asp)](https://www.ncbi.nlm.nih.gov/clinvar/RCV000144615) - NCBI ClinVar database entry for rs4987188.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|73|GPT|1", "source": "prb", "split": "test", "paper_id": "prb73", "comment": "The manuscript’s GWAS linking parental genotypes to transmitted mDNM counts (the *MSH2* and *NEIL2* associations) is not methodologically assessable for confounding because it does not report how population stratification and cryptic relatedness were handled, which materially threatens the validity of the reported associations.\n\n“To determine whether there are variants in the genome that affect the number of mDNMs transmitted by parents to their offspring, we performed a genome-wide association study (GWAS) using the number of mDNMs originating from each parent as a phenotype, adjusting for age, sex, sequencing method and sample type\\(^{32}\\).”\nThis description enumerates several covariates but does not state any approach for controlling ancestry differences (e.g., principal components) or genome-wide relatedness (e.g., mixed models), both of which can induce spurious associations in GWAS settings. This is particularly salient because the phenotype is derived from family data and the cohort is explicitly Icelandic, where extended relatedness is common and can propagate correlation between genotype and phenotype through shared pedigree structure. Without reporting the association model class, the relatedness correction strategy, and the residual inflation diagnostics (or equivalent), it is not possible to judge whether the p-values are well-calibrated. The omission affects the core claim that specific coding variants “increase” genome-wide mDNM counts, because confounding can yield locus-specific signals that resemble true biological effects. Standard practice is to explicitly document these controls because readers cannot infer them from the existence of WGS data or from covariate adjustment alone. As written, the evidence for *MSH2*/*NEIL2* as germline “mutators” is not robustly supported by an adequately specified GWAS methodology.\n“Fig. 1 | Overview of the analysis. We use WGS data from Iceland and UKB and genealogy data from Iceland. From the WGS data we generate microsatellite genotypes. Using trios in the genealogy and the genotypes we detect and phase mDNMs and count the number of mDNMs per trio. We associate the individual mDNM counts with genotypes of the parents in the trios. We compute population wide expected heterozygosity based on the genotypes and observe how it is affected by sequence context. From the phased mDNMs we also estimate age and sex effects on the mDNM rate and to create parental phenotypes based on number of mDNMs found in offspring from the phased mDNMs.”\nThis explicitly links the primary association analysis to genealogy/trio structure, which increases the need to address non-independence among samples and pedigree-driven correlation. In such settings, even modest unmodeled relatedness can inflate association statistics or create apparent signals in regions correlated with family structure. The manuscript does not specify whether the GWAS was performed on unrelated founders, on all parents with a kinship-aware model, or with within-family designs that intrinsically control stratification. The lack of clarity prevents evaluating whether the reported associations reflect biological mutator effects or cohort structure. Because the association results underpin the paper’s headline conclusion about genetic control of microsatellite mutation rate, this missing methodological detail is a major validity concern rather than a reporting nicety. Transparent reporting is also essential for reproducibility because different standard GWAS pipelines can yield meaningfully different results under relatedness.\n“Population stratification--allele frequency differences between cases and controls due to systematic ancestry differences-can cause spurious associations in disease studies.” [\\[1\\]](#ref1)\nThis sentence states the core methodological risk: ancestry-driven allele frequency differences can generate false positive associations if not corrected. While the paper’s phenotype is quantitative and derived from trio-based mDNM counts (not a case-control disease endpoint), the same principle applies because the tested genotype-phenotype correlation can be induced by structure rather than causality. The manuscript does not document a stratification control analogous to PCA or another established approach, so the reader cannot verify that this risk was mitigated. In a large WGS cohort, subtle stratification can be hard to detect without explicit reporting of controls and calibration. Because the reported p-values are central to claiming discovery of mutator variants, the absence of such documentation weakens confidence in the association findings. This directly undermines the validity criterion: uncorrected stratification is a known publication-prohibiting flaw for GWAS-derived causal claims.\n“The additions concern population stratification, genotyping errors, modeling haplotype variation, Hardy–Weinberg equilibrium, replication, selection of participants, rationale for choice of genes and variants, treatment effects in studying quantitative traits, statistical methods, relatedness, reporting of descriptive and outcome data, and the volume of data issues that are important to consider in genetic association studies.” [\\[2\\]](#ref2)\nThis guidance highlights that population stratification and relatedness are not optional implementation details but central considerations for interpreting genetic association results. The manuscript reports several genotype-quality filters and covariate adjustments, yet it does not report methods to assess/address stratification or relatedness, nor does it provide calibration diagnostics. Because the study relies on an Icelandic genealogy-linked design, these concerns are elevated rather than diminished. The absence of these reporting elements blocks a reader from evaluating whether the association is credible under common standards for genetic association studies. This is significant because the paper’s conclusions depend on interpreting two loci as mutators rather than as artifacts of cohort structure. The mismatch between what is expected to be reported for validity assessment and what is actually reported constitutes a major methodological deficiency.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|73|GPT|2", "source": "prb", "split": "test", "paper_id": "prb73", "comment": "The manuscript’s headline estimate of “63.7 mDNMs per offspring per generation” and related “genome-wide” statements rely on extrapolating from a subset of STR loci and trio-marker combinations that are strongly constrained by read-length-driven genotyping limitations, making the absolute genome-wide burden estimate potentially biased and not adequately justified.\n\n“Our microsatellite genotyping is limited by read length (151 bp for most samples), resulting in a decrease in accuracy when detecting and determining genotypes of alleles with long RRTs. While the RRT length limit for inclusion in our study is 140bp, the average expected heterozygosity in our datasets decreases at RRT lengths exceeding 80 bp (Fig. S1, Fig. S2), so we conclude that this is the length where the effect of the RRT length on the genotyping accuracy becomes pronounced.”\nThe manuscript explicitly acknowledges that genotyping accuracy deteriorates for longer repeat tracts, with a pronounced effect beyond ~80 bp, which is precisely where mutation rates can differ and where detection bias is expected. This limitation implies that the analyzed STR set is not a random sample of all microsatellites but is enriched for loci that are short enough to be called reliably in short reads. Any downstream attempt to infer a genome-wide count must therefore model how omitted/poorly genotyped loci differ in both mutability and callability. The paper does not present such a model; instead, it proceeds with a simple scaling/extrapolation. Because the key numerical claim (63.7 mDNMs) is intended as an absolute genome-wide burden comparable to SNP/indel DNM loads, the acknowledged ascertainment bias is not a minor caveat—it can change the magnitude and interpretation of the result. Without demonstrating that excluded loci have similar mutation rates (or providing bounds/sensitivity analyses), the “genome-wide” framing is not sufficiently supported.\n“The trios yielded on average 256,066 microsatellites (40.4%) where all three genotypes passed quality filters and we were able to test for mDNMs.”\nThis indicates that, per trio, mDNM detection is performed on only ~40% of microsatellites, meaning the observed per-trio mDNM count is derived from a substantial and systematically filtered subset. If the missing 60% differs in repeat length, motif composition, genomic context, or mapping quality (all plausible and partially supported by the authors’ own read-length discussion), then simple scaling to the full set can be biased. Moreover, the “available” subset can vary across trios due to sequencing quality and coverage, further complicating extrapolation because missingness may correlate with parental age or other covariates. The manuscript does not quantify how the available-marker subset differs from the total in terms of mutation-prone attributes, nor does it provide uncertainty that reflects this systematic exclusion. Since the absolute mutation burden is a central conclusion, this incomplete and potentially non-representative exposure set is a major threat to validity.\n“Using motif length specific mutation rates and the average number of markers available for each trio to extrapolate to the full set of 1,394,292 microsatellites gives an expected number of 63.7 mDNMs (95% CI: 61.9-65.4) per offspring per generation\\(^{32}\\).”\nThis sentence makes clear that the headline “per offspring” estimate is not directly observed but extrapolated from motif-specific rates computed on a restricted callset. The extrapolation assumes that the measured mutation rates generalize to the unobserved portion of the microsatellite set, despite the authors’ statement that genotyping accuracy decreases substantially for long tracts. The resulting confidence interval is presented as if it captures the dominant uncertainty, but the described procedure (bootstrapping replicates of the observed data) does not automatically account for systematic bias from uncallable loci. This matters for interpretation: the paper uses the extrapolated number to compare mDNM burden to SNP/indel burdens, which could be misleading if the extrapolation undercounts or overcounts mutations in difficult loci. A robust genome-wide estimate typically requires either long-read validation across the relevant length spectrum or an explicit correction model for detection/callability. Neither is documented here, making the genome-wide numerical claim insufficiently supported.\n“Further, since ConSTRain is limited by the sequencing read length it will never be able to genotype alleles that are longer than the read length.” [\\[4\\]](#ref4)\nThis external statement captures a general limitation of short-read STR genotyping: alleles exceeding the read length are intrinsically difficult or impossible to genotype without additional signals or specialized modeling. The manuscript’s own acknowledged drop in accuracy with increasing RRT length is consistent with this limitation, meaning that the analyzed loci are likely truncated at the high-length tail where mutation dynamics can differ. In that context, extrapolating from the callable subset to a “genome-wide” burden requires careful correction for the missing tail and its potentially higher mutation rate. The paper’s extrapolation method does not describe such a correction; it uses motif-length stratification but does not incorporate length-dependent callability beyond the observed set. Therefore, established understanding of short-read STR limits strengthens the concern that the paper’s genome-wide burden estimate is not methodologically secured. This directly affects validity and the robustness of the paper’s quantitative conclusions.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|73|GPT|3", "source": "prb", "split": "test", "paper_id": "prb73", "comment": "The manuscript’s mDNM calling and validation do not adequately resolve homopolymer-associated error modes, even though homopolymers are acknowledged to have elevated false positives and are pivotal to both the reported genome-wide burden and the discovery logic for the *NEIL2* association, undermining the reliability of conclusions.\n\n“Homopolymer mDNMs have a higher false positive rate than other mDNM categories. To assess the robustness of our results, we reran the GWAS on mDNM counts per parent without mDNMs occurring at homopolymers. … Furthermore, we find a novel association between mDNM counts without homopolymers … both in *NEIL2* …”\nThis passage establishes that homopolymers are a recognized high-error subclass and that excluding them changes the set of significant GWAS findings, yielding a new locus (*NEIL2*). When a key discovery depends on removing an error-prone class, the manuscript should demonstrate that the remaining calls are not still affected by related systematic biases (e.g., length-dependent or context-dependent errors) and that the exclusion does not introduce phenotype redefinition artifacts. The paper provides p-values and effect sizes but does not provide a detailed error model explaining why homopolymers are uniquely problematic while other repeat classes are sufficiently well-behaved for association testing. Because the NEIL2 signal is discovered in a sensitivity analysis motivated by technical error, the burden of proof for robustness is higher than for a primary analysis, not lower. Without deeper validation and calibration, it remains unclear whether the NEIL2 association reflects biology or residual detection artifacts correlated with genotype or batch effects. This undermines the conclusions about a second “mutator” allele.\n“To estimate the false positive rate of our method we used two methods; PacBio CCS sequence data, available for four of our trios, and mDNM sharing in nine Icelandic monozygotic twin pairs in our set. We used haplotype resolved assemblies of the PacBio data and while we were unable to verify homopolymer mDNMs as the PacBio sequencing error rate was too high\\(^{71}\\) we were able to verify the existence of 27 mDNMs with motif length >1.”\nThe orthogonal validation dataset is extremely small (four trios for PacBio), and crucially it cannot validate the homopolymer category at all—the category explicitly flagged as having higher false positives. As a result, the paper’s main validation pathway does not directly quantify the error rate for the subset most likely to inflate genome-wide burden estimates or distort derived phenotypes. Validating only 27 non-homopolymer events provides limited assurance about global error properties, especially for rare systematic artifacts that can accumulate across hundreds of thousands of loci. The manuscript’s downstream analyses (including extrapolated genome-wide burden and association testing) implicitly assume that residual error is either small or uncorrelated with predictors; this is not established for homopolymers. The inability to verify homopolymers with the chosen long-read technology also suggests that alternative orthogonal strategies (e.g., targeted assays) are necessary if homopolymers materially contribute to summary estimates. Without such validation, homopolymer-driven uncertainty is not properly reflected in the conclusions.\n“Notably, the transmission rate for homopolymers is only 0.4 while the other motif lengths have transmission rates much closer or equal to 0.5.”\nA transmission rate substantially below 0.5 for putative germline DNMs is consistent with a high fraction of false positives or other systematic misclassification for that motif class. This is not a subtle deviation: a value of 0.4 implies a sizable discordance relative to Mendelian expectations, which should directly affect any estimate of genome-wide mDNM counts that includes homopolymer calls. Yet the manuscript still presents a precise-appearing genome-wide burden estimate and confidence interval without explicitly propagating a homopolymer-specific uncertainty term. It also implies that mDNM phenotypes used in GWAS could differ in measurement error structure across individuals depending on how many homopolymer loci are “available” and how errors vary across samples. Because the paper uses homopolymer exclusion as a robustness check that changes the discovered locus set, this empirical sign of homopolymer-specific error should be treated as a central methodological limitation. The current treatment is insufficient to support strong causal conclusions.\n“Altogether, about 47% of errors are due to homopolymers.” [\\[5\\]](#ref5)\nThis statement from an independent error-characterization study underscores that homopolymer-associated error can be a dominant contributor to sequencing inaccuracies in long-read contexts. While the technology and basecaller studied there differ from the Illumina and PacBio data in this manuscript, the general point is that homopolymers are a pervasive and difficult error mode that often requires dedicated handling and validation. The manuscript’s own inability to validate homopolymer mDNMs with PacBio and its observation of reduced transmission for homopolymers align with this broader understanding. Therefore, treating homopolymers as a simple subset to exclude (without deeper quantification of how much they distort genome-wide estimates and association phenotypes) is not sufficient for robust inference. The external evidence strengthens the argument that homopolymer uncertainty is likely substantial and should be explicitly modeled or bounded. Without that, key conclusions remain vulnerable to technical artifacts.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|73|GPT|4", "source": "prb", "split": "test", "paper_id": "prb73", "comment": "The paper’s main findings (mDNM callset generation, phasing, phenotype construction, and GWAS leading to *MSH2*/*NEIL2*) are not reproducible from the provided code/materials because the repository primarily documents STR genotyping and the manuscript does not provide actionable access to intermediate datasets or complete analysis scripts.\n\n“We generated two large microsatellite genotype sets. The microsatellite genotypes for the UKB samples are publicly available and have been tested for association with various phenotypes\\(^{49}\\).”\nThis asserts public availability of a core resource but provides no accession, persistent identifier, or retrieval instructions within the manuscript text provided here. Without a concrete pointer to where and how the UKB STR genotypes can be obtained (and under what access terms), an independent researcher cannot reproduce downstream results even if they have UKB access. Moreover, the headline mutator results are derived from the Icelandic trio set, which is not described as publicly accessible in a way that would enable independent reproduction. Reproducibility in genomics often requires at least release of summary statistics, derived phenotypes, and detailed pipelines even when raw data are controlled-access. The manuscript does not provide such materials in the main text, limiting verification of results. This is a significant barrier to assessing reliability because the claims depend on complex multi-step processing.\n```text\n## Running popSTR\n\nTo genotype samples listed in `bamList` for all markers on `chrom` in parallel where the number of markers run by each job is equal to `markersPerJob` :\n\n    runPerChrom bamList reference chrom markersPerJob\n```\nThe provided code documentation focuses on running the popSTR genotyper to generate STR genotypes from BAM/CRAM inputs, which is only the first step in the paper’s end-to-end workflow. The manuscript’s central scientific claims require additional steps: de novo detection in trios, parent-of-origin phasing, construction of per-parent mDNM phenotypes, and GWAS association testing. Those downstream steps are not documented in the code materials shown here, and the codebase does not provide an executable pipeline that reproduces the reported figures, association p-values, or effect-size translations to “genome-wide mDNMs.” As a consequence, even a well-resourced reader cannot audit how genotype filters, missingness, and error handling propagate into the association phenotype. This gap affects not just convenience but also scientific validity, because small implementation choices in de novo STR calling can materially change mDNM counts and their correlates. Therefore, the provided code is insufficient for reproducing the paper’s primary conclusions.\n“All scholarly digital research objects—from data to analytical pipelines—benefit from application of these principles, since all components of the research process must be available to ensure transparency, reproducibility, and reusability.” [\\[6\\]](#ref6)\nThis statement articulates a widely accepted standard: reproducibility depends on availability of not only raw data but also the computational workflows that transform inputs into published claims. The present manuscript provides substantial detail on STR genotyping and some statistical models, but it does not provide an end-to-end, runnable analysis pipeline or the derived intermediate artifacts needed to replicate the conclusions. When key steps are missing, readers cannot validate whether findings are robust to alternative (but reasonable) implementation choices, nor can they reproduce exact association statistics. In controlled-access genomics, full reproducibility is often addressed by releasing derived callsets, summary statistics, and scripts, even if raw reads are restricted. The paper’s current materials fall short of this expectation, impeding independent verification. This shortcoming directly impacts the “Data and methodology” criterion and weakens confidence in the reported conclusions.\n“Availability of raw data may help interested investigators reproduce the published analyses and also pursue additional analyses.” [\\[2\\]](#ref2)\nThis guidance highlights that reproducibility and downstream scientific utility depend on explicit data availability pathways. In this manuscript, the main numerical and association results are computed from large WGS datasets and de novo calls that are not included as downloadable artifacts in the provided materials. Even if raw data access is restricted (which is common), standard practice is to provide at least summary-level outputs (e.g., GWAS summary statistics for *MSH2*/*NEIL2*, mDNM call definitions and per-sample phenotypes, and scripts) so that independent researchers can validate claims. The manuscript does not provide these artifacts in a citable, persistent way within the provided content. This limits the community’s ability to check calibration, replicate results, and build on the findings. The gap therefore represents a major reproducibility issue rather than a documentation preference. It also complicates interpretation because unverifiable computational steps can hide unrecognized biases.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|73|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb73", "comment": "The paper reports a genome-wide microsatellite mutation rate of 63.7 mDNMs per generation but fails to adequately account for the high false positive rate (11.3%) observed in homopolymers, which constitute a significant portion of the detected mutations.\n\n\"Homopolymer mDNMs have a higher false positive rate than other mDNM categories.\"\nThe authors acknowledge that homopolymers are prone to higher error rates, which is a known issue in STR genotyping due to polymerase slippage during sequencing.\n\"we were unable to verify homopolymer mDNMs as the PacBio sequencing error rate was too high\"\nThis indicates a lack of independent validation for the most error-prone class of STRs using long-read sequencing, relying instead on indirect methods like twin concordance.\n```\nTable S31 Sharing of mDNMs between monozygotic twins stratified on motif length.\nMotif length (bp) Shared Not shared Error rate\n1 47 6 11.3%\n```\nThe table shows an error rate of 11.3% for motif length 1 (homopolymers), which is significantly higher than for other motif lengths (e.g., 5.3% for dinucleotides, 0% for tetranucleotides). Given that homopolymers account for ~22% of the total mDNMs (17,194 out of 76,987, Table 1), an 11.3% error rate implies nearly 2,000 false positives in this category alone. The paper does not explicitly state that the final estimate of 63.7 mDNMs was corrected for this specific error rate, potentially leading to an overestimation of the total mutation load.\n```\nTable S26 Per motif length enrichment of mDNMs between maternally and paternally phased mDNMs.\nMotif length (bp) Maternal Paternal Maternal percentage\n1 2,962 5,141 36.6%\n```\nMaternal mDNMs are enriched in homopolymers (36.6% of maternal mDNMs are homopolymers vs. 14.5% of paternal mDNMs). If homopolymers have a high false positive rate, the maternal mutation rate and the maternal age effect might be disproportionately affected by genotyping errors compared to the paternal rate.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|73|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb73", "comment": "The paper claims a novel association between a synonymous variant in `NEIL2` (rs8191642) and the paternal mDNM rate but fails to provide sufficient functional evidence (e.g., eQTL analysis or experimental validation) to support a causal mechanism, relying instead on speculation about replication timing.\n\n\"we find a novel association between mDNM counts without homopolymers and two correlated (\\(r^2\\)=0.988) SNPs, rs8191642... a synonymous variant (Pro188), and rs8191649... an intronic variant, both in *NEIL2*\"\nThe identified variants are synonymous and intronic, which are typically non-causal unless they affect splicing or expression levels. The paper does not present evidence that these specific variants are functional.\n\"it is likely that the association between the synonymous variant in *NEIL2* and the number of paternally transmitted mDNMs is due to the more frequent replication of spermatogonia.\"\nThis statement is speculative. While `NEIL2` is a plausible candidate gene due to its role in DNA repair, the specific variant's effect is unproven. The authors should have checked public databases like GTEx [3] to see if rs8191642 is an eQTL for `NEIL2` in relevant tissues (e.g., testis), or performed functional assays. Without such evidence, the association might be driven by a different causal variant in linkage disequilibrium.\n\nReferences:\n[3] [The GTEx Consortium atlas of genetic regulatory effects across human tissues](https://www.science.org/doi/10.1126/science.aaz1776)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|73|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb73", "comment": "The provided code repository contains scripts for genotyping and basic processing but lacks the code for the key statistical analyses, including the Poisson regression models for parental age effects and the GWAS for genetic determinants, hindering the reproducibility of the study's central findings.\n\n\"Association analysis was performed by SK, TR and BVH. Age effect regression model was implemented by HJ.\"\nThe methods section describes complex statistical models, including Poisson regression with covariates and a GWAS. However, the code repository (as listed in the file structure) only contains scripts like `run.sh`, `msGenotyper.cpp`, and `popSTR.cpp`, which are for genotyping.\n\"Code/ run.sh\"\nThe `run.sh` script only calls `runPerChrom.sh`, which appears to be a wrapper for the genotyping pipeline. There are no R or Python scripts visible that correspond to the regression analysis or the GWAS described in the text. Reproducibility requires access to the exact code used to generate the statistical results and figures.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|73|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb73", "comment": "Although the paper’s results seem interesting and plausible, the paper is hindered by a lack of methodological detail. In some cases, key details are supplied in the supplement, but are omitted from the main text in a misleading or confusing way. In other cases, the underlying analysis may not be rigorous enough for the results to pass muster.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|73|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb73", "comment": "One weakness of the paper with potentially far reaching downstream consequences is a failure to estimate an accurate false positive rate for homopolymer mutations. The authors note that even HiFi data has a high error rate at homopolymer loci, and short read data certainly has a higher error rate at these loci compared to repeats of motif length greater than 1. The transmission rate of 0.4 at homopolymer mutation sites suggests that at least 20% of homopolymers calls are likely to be false positives. The number of false positives is actually higher than this in all likelihood, since third generation transmission is unable to detect false positives that are caused by allelic dropout, i.e. genotyping errors in the parents that cause variants transmitted to the offspring to falsely look like de novo mutations. Allelic dropout also invalidates the premise of the monozygotic twins analysis, since a genotyping error in one of the parents of a set of twins may cause the same false positive de novo mutation to be called in both twins.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|73|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb73", "comment": "To tighten up their validation scheme, the authors need to discuss the possibility of allelic dropout and attempt to minimize it perhaps by requiring that a variant called as a de novo mutation in a child has no supporting reads in either parent. They also need to discuss the results of the validation in the main text (including the percentage of each type of variants that validate by each method) rather than confining the results of these tests to the supplement. Finally, they need to mention much earlier in the manuscript that homopolymer mutations have poor validation rates, disclose how many of their calls are homopolymer mutations, and put error bars around all mutation rate estimates that reflect the high error rate of homopolymer mutations. Could false positive homopolymer mutations be responsible for the apparently enrichment of maternal mutations for homopolymer variants?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|73|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb73", "comment": "Another analysis that is lacking in methodological detail is the fine mapping component of the GWAS. The authors never explain how they narrow down their first peak to a single SNP in MSH2, or how they narrow down their second peak to a synonymous SNP in NEIL2 (which being synonymous seems unlikely to have a large functional effect). My impression is that the typical GWAS peak is associated with quite a wide confidence interval containing several genes. I assume that the authors picked MSH2 and NEIL2 from within larger confidence intervals because of these genes’ prior associations with microsatellite instability, which is reasonable, but the paper needs to be more transparent about how the selection was done, how many other genes are within the peak confidence interval, and whether any of them have functions related to DNA repair or other processes that could impact microsatellite mutation rates.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|73|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb73", "comment": "Finally, given that the central point of this paper is to measure a microsatellite mutation rate, I was struck by the fact that the abstract does not actually mention a mutation rate, but only a raw count of de novo mutations per genome per generation. At several points, the paper mentions “high quality” microsatellites and alludes to the fact that the authors only call mutations at a subset of high quality loci, but this is not discussed at length enough to make it obvious how the raw number of mutations per genome per generation is translated into a mutation rate per locus. A supplementary note also mentions that the sample size of the cohort affects the mutation rate measurement, which seems counterintuitive and is not something that is true of SNV mutation rate measurements. I think it would be more appropriate for the main text to discuss estimation of a mutation rate per locus per generation in a manner that is comparable to other studies, given that this is a central challenge addressed by papers that estimate single nucleotide de novo mutation rates.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|73|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb73", "comment": "In general, the methods used are straight-forward and add important knowledge regarding germline rates of microsatellite mutation in humans. Parental biases in microsatellite mutation have been documented for a few microsatellites that cause disease, and this study now provides a genome-wide analysis of parental biases (sex and age) which is an important advancement. However, while the GWAS section is potentially the most innovative and biologically significant section of the study, insufficient evidence is provided to support the stated major conclusion that this study shows the “microsatellite mutation rate in humans is in part under genetic control”. The authors overinterpret and overstate the significance of the GWAS results, and additional data are required to support the conclusion that the identified variants in MSH2 (rs4987188) and NEIL2 (rs8191642) are “microsatellite mutators”. The authors state (lines 211-215; Supplementary note 9) that their results of an association between the variants and mutation are confined to microsatellites, as they found no association with base substitution mutational signatures. If true, this would be an unprecedented result, because no genetic mutation that solely impacts microsatellite mutation without impacting single nucleotide substitutions or indels has been demonstrated in over 2 decades of microsatellite mutation research. The alternative explanation of their results is that the SNP associations have no mechanistic impact on mDNMs. Because of this, it is imperative that the same results be shown by another approach (for instance, an experimental model system).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|73|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb73", "comment": "Association of mDMN incidence with DNA repair gene SNPs. This is the weakest section of the study. The MSH2 missense variant has been studied in a yeast model (references 46 and 47). In these publications, it was shown that the variant is functional (able to complement an MSH-deficient cell), and the authors of ref. 47 conclude that any impact on mutation rates would be due to levels of protein expression. In the current study, Kristmundsdottir et al. provide no data showing that expression of the MSH2 variant protein is altered, compared to wild-type. Furthermore, they found no association of the variant allele with cancer risk (as would be expected for a defective MSH2 allele), suggesting the variant is functioning normally in maintaining genome stability. The association with the NEIL2 variant is not compelling. This is a synonymous variant and no literature exists to demonstrate this SNP alters NEIL2 function. Furthermore, no evidence is provided by the authors or cited from the literature to support a role for NEIL2 and base excision repair in microsatellite mutagenesis.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|73|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb73", "comment": "The manuscript’s methods should be improved to provide more transparency and allow others to reproduce the results. For the RRT, did the authors use a lower limit for the number of repeat units to define a microsatellite (e.g., were 2 unit motifs as in GG included)? Was this lower limit the same for all units (mono, di, tri, etc)? This is important, as published microsatellite analyses use different definitions. At the other end, was there an upper limit to the RRTs? The authors imply(lines 85-88) that genotypes above 80 bp were unreliable, so was 80bp the upper limit for all STRs? Lastly, lines 463-464 state that WGS regions were removed/excluded. The authors should provided the number of bases or % of the whole genome sequence that were actually included in the analyses.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|73|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb73", "comment": "The authors should discuss the limitations of this study. Findings from a population of ~6,000 Icelandic individuals might not be generally applicable to other populations.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|74|Claude|2", "source": "prb", "split": "test", "paper_id": "prb74", "comment": "The paper claims to discover 130,657 novel deletions and 197,008 novel duplications not present in the existing 1000g-SV catalogue, with high validation rates (0.87 and 0.85 respectively). However, the validation methodology is not clearly described, and the validation appears to be performed on the same 34 HGSVC2 samples used for training the machine learning model, potentially creating circularity in the evaluation.\n\n\"Figure 7: Comparison between the 1000g-SV and SurVIndel2 datasets... Between parentheses, the validation rates of calls in samples with long reads.\" (Figure caption, line 139)\nThe figure caption indicates that validation rates are computed only from \"samples with long reads,\" which are the 34 HGSVC2 samples plus HG002. The paper does not clarify how many of the 130,657 and 197,008 unique variants actually fall within these 35 samples or how representative this subset is of the full 3,202-sample catalogue.\n\"The machine learning model of SurVIndel2 was trained using the 34 samples in HGSVC2 sampled by the NYGC.\" (Methods, line 104)\nThe same samples used for training the random forest classifier are also used for validation. While leave-one-out cross-validation addresses sample-level independence, variants at the same genomic loci appear across multiple samples, potentially creating data leakage. Additionally, the validation rates reported for novel calls are based on this same benchmark, creating potential circularity.\n\"Furthermore, SurVIndel2 predicts 130,657 deletions not present in 1000g-SV, with high validation rate (0.87).\" (Results, line 144)\nThe paper does not explain how a validation rate was computed for these 130,657 deletions. If the validation uses the HGSVC2 benchmark as a reference, the variants would need to exist in the benchmark to be validated. Truly novel variants by definition would not exist in HGSVC2, raising questions about what exactly is being measured. Literature on SV validation emphasizes that \"[l]ong read SV calls are ideal for confirming SV events with accurate breakpoint resolution\" [[1]](#citation-list), but the paper does not describe whether re-alignment of long reads or de novo calling was performed for validation.\n\nReferences:\n[1] [All of Us Short-Read Structural Variant Quality Report - Research All of Us](https://support.researchallofus.org/hc/en-us/articles/27496716922900-All-of-Us-Short-Read-Structural-Variant-Quality-Report-Archived-C2022Q4R9-offcycle-CDRv7)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|74|Claude|3", "source": "prb", "split": "test", "paper_id": "prb74", "comment": "The random forest classifier was trained exclusively on samples sequenced by a single center (NYGC) using a single platform (NovaSeq 6000) at similar coverage (~30x), yet the paper claims the model generalizes well based on testing with only one sample (HG002) sequenced under different conditions.\n\n\"The datasets used for training the model are very homogeneous: they were all sequenced by one sequencing center (NYGC), with the same platform (Illumina NovaSeq 6000), with the same sequencing depth (30x, except for one which was 60x), which can lead to overfitting.\" (Results, line 110)\nThe authors acknowledge this limitation themselves. Sequencing center effects, platform-specific error profiles, and coverage-dependent features could all be learned by the random forest, potentially limiting generalization to data from other sources.\n\"However, the HG002 sample confirms that this is not the case for our model. HG002 was sequenced by a different entity (GIAB Consortium) using a different platform (Illumina HiSeq 2500) and its depth is different (50×).\" (Results, line 110-112)\nRelying on a single sample to demonstrate generalization is insufficient. N=1 provides no estimate of variance or reliability across different sequencing conditions. Machine learning literature indicates that leave-one-out cross-validation can exhibit distributional bias [[2]](#citation-list), and demonstrating generalization typically requires held-out test sets that are truly independent and representative.\n\"The filtering model we provide was trained on the CNVs called from the 34 human samples. We call this the default model. For this reason, we are interested in (i) how SurVIndel2 performs on different organisms using the default model...\" (Section 2.4, line 124)\nThe authors test cross-organism generalization extensively (Arabidopsis, cattle, mouse, rice) but do not similarly test cross-platform or cross-center generalization within humans. Given that the tool is intended for use on diverse human datasets, this represents a gap in the evaluation.\n\nReferences:\n[2] [Distributional bias compromises leave-one-out cross-validation - arXiv](https://arxiv.org/abs/2406.01652)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|74|Claude|4", "source": "prb", "split": "test", "paper_id": "prb74", "comment": "The paper uses a random forest classifier with approximately 50 features but does not report feature importance analysis, making it unclear whether hidden split reads, statistical tests, or other features are the primary drivers of improved performance.\n\n* Quote (from code, features.py, lines 7-57):\n```python\nfeature_names = [\n    'svtype',\n    'source',\n    'svlen',\n    'median_depths[0]',\n    ...\n    'ks_pval',\n    ...\n    'clipped_reads[0]',\n    'clipped_reads[1]',\n    ...\n]\n```\nThe code reveals that approximately 50 features are used, including depth-based features, discordant pair features, Kolmogorov-Smirnov p-values, clipped read counts, and junction scores. Without feature importance analysis, readers cannot assess which features contribute most to classification decisions.\n\"Additionally, we use the distribution of the insert sizes of the read pairs around the CNV to calculate a confidence interval for its size, as well as a p-value estimating the probability that the CNV is a false positive.\" (Methods, line 91)\nThe KS test p-value is mentioned as a feature, but without feature importance analysis, it remains unclear whether this statistical feature contributes meaningfully to the classification, especially given that the statistical tests are not applied to duplications.\n\"The second tests employs a Kolmogorov-Smirnoff test to calculate a p-value estimating whether C and D are significantly different.\" (Supplementary Methods, line 425)\nThe statistical test features are described in detail, suggesting they are important to the methodology. However, for the random forest to learn useful patterns from these features, they must provide discriminatory power. Feature importance would reveal whether the claimed methodological innovations (hidden split reads, statistical testing) actually contribute to performance, or whether simpler features like depth or read counts dominate. This is a standard practice in machine learning-based bioinformatics tools [[3]](#citation-list).\n\nReferences:\n[1] [All of Us Short-Read Structural Variant Quality Report - Research All of Us](https://support.researchallofus.org/hc/en-us/articles/27496716922900-All-of-Us-Short-Read-Structural-Variant-Quality-Report-Archived-C2022Q4R9-offcycle-CDRv7)\n[3] [Understanding overfitting in random forest for probability estimation - PMC](https://pmc.ncbi.nlm.nih.gov/articles/PMC11437774/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|74|Claude|5", "source": "prb", "split": "test", "paper_id": "prb74", "comment": "The paper compares SurVIndel2 primarily against Manta, Delly, Lumpy, and the original SurVIndel, but does not include more recent state-of-the-art methods such as DRAGEN (a widely-used commercial solution) in the main benchmarking, limiting the assessment of SurVIndel2's relative position in the field.\n\n\"We use these datasets to benchmark the performance of SurVIndel2, and three highly cited methods that performed well in a recent benchmarking analysis [4]: Delly [19], Lumpy [12]... and Manta [5].\" (Methods, line 102)\nWhile these methods are indeed widely cited, they are not necessarily the current state of the art. Recent benchmarking studies have shown that DRAGEN outperforms many open-source tools for SV detection [[4]](#citation-list), yet DRAGEN is not included in the main comparison.\nFrom the published Nature Communications version (not in the preprint, but from search results): \"Furthermore, we compared SurVIndel2 to the SV calling module in DRAGEN... Our benchmarks demonstrate that although DRAGEN is a marked improvement over Manta, it does not achieve the same level of sensitivity and precision as SurVIndel2.\" [[5]](#citation-list)\nThe published version includes DRAGEN comparison in supplementary materials, but the preprint under review does not include this comparison. For a comprehensive evaluation of the method's contribution, comparison against the current commercial state of the art should be presented.\n\"DRAGEN also reports CNVs, which include larger deletions and duplications... For CNVs with lengths in the range of 1–5 kbp and 5–10 kbp, DRAGEN performed substantially better, with F-measures of 92.60%... and 96.60%...\" [[6]](#citation-list)\nRecent literature demonstrates that DRAGEN achieves very high F-measures for CNV detection. Without direct comparison in the main results, readers cannot assess whether SurVIndel2's improvements represent a substantial advance over current best practices or are incremental gains over older methods.\n\nReferences:\n[4] [A Hitchhiker Guide to Structural Variant Calling - PMC](https://pmc.ncbi.nlm.nih.gov/articles/PMC12383524/)\n[5] [SurVIndel2: improving copy number variant calling from next-generation sequencing using hidden split reads - Nature Communications](https://www.nature.com/articles/s41467-024-53087-7)\n[6] [Comprehensive genome analysis and variant detection at scale using DRAGEN - Nature Biotechnology](https://www.nature.com/articles/s41587-024-02382-1)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|74|GPT|2", "source": "prb", "split": "test", "paper_id": "prb74", "comment": "This paper’s conclusion that SurVIndel2 yields a substantially more complete 1000 Genomes CNV catalogue with “high validation rate” is insufficiently supported because the validation is reported only “in samples with long reads” that overlap the HGSVC2 cohort used to train and benchmark SurVIndel2’s filtering model, making the validation non-independent and potentially optimistic.\n\n“The machine learning model of SurVIndel2 was trained using the 34 samples in HGSVC2 sampled by the NYGC. For this reason, when testing them, we use a leave-one-out strategy.”\nLeave-one-out within the same 34-sample cohort reduces direct per-sample label leakage, but it does not provide an independent external validation of the learned filtering behavior. The training and evaluation data share the same sequencing center, platform, library preparation, and mapping pipeline characteristics, which the paper itself notes can create homogeneity and risk overfitting. When the same cohort is then used to compute “validation rates” for catalogue-level claims, the evaluation can become circular: the model is tuned to maximize agreement with long-read-derived calls in this cohort, and the reported validation is measured against those same long-read resources. This can inflate validation metrics relative to genuinely independent samples or platforms and makes it hard to extrapolate to the full 3,202-sample catalogue. A stronger design would validate the 1000 Genomes discoveries on long-read samples not used in model training/tuning, ideally sequenced and processed independently. Without that, “high validation rate” is not necessarily evidence of generalizable correctness.\n“Between parentheses, the validation rates of calls in samples with long reads.”\nThis captioned evaluation explicitly restricts validation-rate reporting to a subset of samples with long-read data, rather than validating across the full cohort. If the long-read subset is largely the HGSVC2 set (as implied by the repeated use of HGSVC2 for benchmarking and validation throughout), then the validation statistic is computed on the same distribution used to build and evaluate the classifier. Even if many calls are rare, the selection of validated samples and genomic contexts can materially bias estimated validation upward or downward. For a population-scale callset claim, readers need to know how validation varies across populations, sequencing batches, and mapping contexts, not only within a curated long-read subset. The paper does not provide uncertainty estimates or stratified validation for the novel-event component (e.g., by repeat context, size, or allele frequency) in an independent validation cohort. As a result, the catalogue-level completeness claims are less robust than they appear.\n“Furthermore, SurVIndel2 predicts 130,657 deletions not present in 1000g-SV, with high validation rate (0.87). … SurVIndel2 predicts an additional 197,008 duplications, with high validation rate (0.85).”\nThese large absolute numbers are a central conclusion of the paper, so the evidentiary standard should be particularly high. The validation rates are presented as though they generalize to the catalogue’s novel events, but the text ties validation to “samples with long reads,” which are a small fraction of the 3,202 genomes. If validation is computed only where long reads exist, it may systematically miss cohort-specific artifacts (e.g., platform- or mapping-related false positives) present elsewhere in the 3,202 sample set. Additionally, because the classifier was trained on the HGSVC2 cohort, agreement with long-read truth in those individuals is partly an expected consequence of the training objective, not an external check. Common practice in benchmarking emphasizes using test sets that were not used to train or optimize pipelines to avoid optimistic estimates of precision/recall. Without an external validation cohort, the conclusion that these hundreds of thousands of additional events are genuinely high-confidence remains insufficiently substantiated.\n“Additionally, the pipelines that generated the variant calls could be tuned to HG001, which, in many situations, was used to train or optimize pipelines.” ([[1]](#ref1))\nThis observation from benchmarking best practices highlights a well-known pitfall: performance estimates can be inflated when a benchmark sample (or closely related sample cohort) is used to tune or train methods. The same risk applies here at the cohort level: SurVIndel2’s filtering model is trained on HGSVC2 samples, and catalogue validation appears to be judged using long-read data from the same or closely related HGSVC2 cohort. Even with leave-one-out, repeated model development decisions (feature design, filter thresholds, and model structure) can be influenced by aggregate performance on the benchmark cohort. This makes catalogue-level validation less independent than readers might assume. Independent validation (different sequencing centers/platforms, different individuals with orthogonal long-read truth) is typically needed to establish that high validation rates are not a byproduct of benchmark-specific tuning. The paper’s current evidence does not clearly meet that standard for the “hundreds of thousands” novel-event claim.\n\nReferences:\n[1] [Krusche et al., “Best Practices for Benchmarking Germline Small Variant Calls in Human Genomes,” *Nature Biotechnology* (2019)](https://pmc.ncbi.nlm.nih.gov/articles/PMC6699627/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|74|GPT|3", "source": "prb", "split": "test", "paper_id": "prb74", "comment": "This paper’s cross-organism performance claims are weakened because its non-human “benchmark catalogues” are defined as Sniffles2 callsets on PacBio HiFi reads without demonstrating that these callsets constitute a high-confidence truth set with defined benchmark regions, which threatens the validity of sensitivity/precision comparisons.\n\n“We generated a benchmark dataset by using Sniffles2 [24] on PacBio HiFi reads for the same samples.”\nRunning a single SV caller on long reads is a reasonable way to obtain candidate variants, but it is not equivalent to a benchmark truth set unless additional integration/adjudication steps are performed. Long-read callers—including state-of-the-art tools—still have non-trivial error modes in repetitive contexts, for duplications, and for complex events, and the paper does not describe any multi-method integration, manual curation, or orthogonal validation for these non-human truth sets. Without defining confident regions (where extra calls are presumed false positives) and without assessing false discovery in the “truth,” computed precision and sensitivity for short-read callers can be biased. In particular, methods that differ from Sniffles2’s representation, breakpoint placement, or SVTYPE conventions may be penalized even when they are correct, while methods that match Sniffles2 may appear better by construction. This issue is amplified when making broad claims that the default (human-trained) model “works well for every tested organism.” A more robust evaluation would use integrated truth sets (multiple callers/technologies) or assembly-based validation, and would specify benchmark regions where false positives can be identified reliably.\n“Benchmark catalogues were obtained by running Sniffles2 on PacBio HiFi reads.”\nThis statement makes explicit that the “benchmark” is not an experimentally validated reference but the output of one algorithm. Because the same paper is comparing SurVIndel2 (a short-read caller) against other short-read callers, any incompleteness or bias in Sniffles2’s callset will propagate into all reported metrics and may reverse method rankings in certain contexts. For example, if Sniffles2 under-calls certain tandem duplications or has systematic breakpoint biases in repeats, then all tools will appear to have low sensitivity or precision in those categories irrespective of true performance. The paper does not report independent verification of Sniffles2’s correctness in these organism-specific benchmarks, nor does it quantify uncertainty due to truth-set error. As a result, the conclusion that SurVIndel2 “performs better for every organism” is not adequately supported by a benchmark of known accuracy. This is a significant methodological gap because the cross-organism claim is used to argue generalizability of the approach.\n“Here we present Sniffles2, which improves over current methods by implementing a repeat aware clustering coupled with a fast consensus sequence and coverage-adaptive filtering.” ([[3]](#ref3))\nEven though Sniffles2 is explicitly presented as an SV calling method (i.e., an estimator), the paper treats its output as a benchmark catalogue in multiple organisms without additional truth-set construction steps. The Sniffles2 abstract frames it as improving over “current methods,” which implies it still has definable errors and is not an oracle. Benchmarks built from a single caller’s output risk conflating agreement with that caller with correctness, which is especially problematic when the reviewed paper’s key claim is improved sensitivity/precision. This is precisely why high-confidence SV benchmarks in the community typically integrate multiple methods and technologies, rather than adopting one caller output as truth. Without such integration, precision estimates can be inflated (if false positives are in the truth) or deflated (if true variants are missing from the truth). The methodological choice therefore undermines the strength of the cross-organism generalization claims.\n“To create this benchmark for a broadly consented son in a Personal Genome Project trio with broadly available cells and DNA, the Genome in a Bottle (GIAB) Consortium integrated 19 sequence-resolved variant calling methods from diverse technologies.” ([[2]](#ref2))\nThis sentence illustrates the community standard for building benchmark truth sets: integrate many callsets across diverse technologies to reduce biases of any single method. The paper under review does not follow an analogous approach for its non-human benchmarks, even though long-read SV calling accuracy can vary substantially by genome context and SV type. GIAB’s approach also couples the benchmark VCF with benchmark regions, enabling identification of false positives (extra calls) and false negatives (missed calls) in a principled manner. In contrast, a single-caller Sniffles2 callset does not by itself define where extra calls should be counted as false positives, which complicates any precision calculation. Therefore, the paper’s non-human benchmark design is substantially weaker than established best practices for benchmarking variant callers. This discrepancy is large enough to affect the validity of the paper’s claims about cross-organism performance.\n\nReferences:\n[2] [Zook et al., “A robust benchmark for detection of germline large deletions and insertions,” *Nature Biotechnology* (2020)](https://pmc.ncbi.nlm.nih.gov/articles/PMC8454654/)\n[3] [Smolka et al., “Detection of mosaic and population-level structural variants with Sniffles2,” *Nature Biotechnology* (2024)](https://pubmed.ncbi.nlm.nih.gov/38168980/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|74|GPT|5", "source": "prb", "split": "test", "paper_id": "prb74", "comment": "This paper’s reproducibility is materially limited because the ML-based filtering central to SurVIndel2’s claimed precision improvements depends on external training data/models and a non-deterministic training procedure, and the codebase includes x86-specific SIMD headers that can prevent building core executables on non-x86 systems, conflicting with the paper’s claim that the tool is easy to run from BAM/CRAM input alone.\n\n“SurVIndel2 is fully open source and available at https://github.com/kensung-lab/SurVIndel2 It is easy to run and only requires a BAM or a CRAM file and a reference genome, and it outputs a fully standard VCF file.”\nThis statement sets an expectation that the tool can be built and executed straightforwardly across common environments using only alignment files and a reference. However, the method description and repository indicate that performance depends on an ML filtering model (“pre-trained random forest”), and building/running requires compiled auxiliary binaries, which makes the real dependency surface larger than described. If the ML model and its training data are not fully specified and easily obtainable, users cannot reproduce the filtering behavior that underpins the paper’s precision claims. Additionally, the “easy to run” claim is undermined when platform-specific compilation issues prevent building the required executables, which can block end-to-end execution even for the provided demo. Reproducibility in computational genomics typically requires explicit versioning of models, deterministic training, and platform-compatible builds or containers. The paper does not provide sufficient detail to ensure those conditions.\n“Download the file ml-training-data.zip from the latest release, and place it within the SurVIndel2 folder.”\nRequiring a separately downloaded training dataset (not bundled with the code and not described in the paper’s Data availability section) introduces a key reproducibility bottleneck. Readers attempting to reproduce the paper’s exact benchmark results need the precise training data, the exact feature extraction pipeline, and the exact model hyperparameters used, but this workflow is not fully specified in the manuscript. If the “latest release” changes over time, the contents of ml-training-data.zip can change, producing different trained models and thus different calls and performance metrics. This undermines long-term reproducibility and makes it difficult for third parties to validate the reported sensitivity/precision improvements. A more reproducible approach would archive the exact training data and the trained model artifact(s) with immutable identifiers and document them in the paper. As written, the pipeline to reach the reported classifier-filtered performance is not fully pinned.\n```python\nclassifier = RandomForestClassifier(n_estimators=cmd_args.n_trees, max_depth=15, n_jobs=-1)\nclassifier.fit(training_data[sources], training_labels[sources])\n```\nThe training code does not set `random_state`, so model training can be non-deterministic across runs, platforms, or library versions. For a method whose reported advantage depends strongly on ML-based filtering to control false positives, non-deterministic training complicates reproducibility of both the model and any downstream benchmark numbers. This is not merely a cosmetic issue: small changes in the random forest can change decision boundaries, especially in imbalanced classification settings common in SV filtering, which can change precision/recall. Without a fixed seed and version-pinned dependencies, reproducing the exact model used for the paper’s results is difficult even with the same training data. The manuscript does not report a seed, a trained-model checksum, or a deterministic build procedure. Therefore, the computational evidence supporting the conclusions is harder to independently verify.\n“To obtain a deterministic behaviour during fitting, `random_state` has to be fixed.” ([[4]](#ref4))\nThis scikit-learn documentation directly explains why omitting `random_state` undermines determinism of the reported ML filtering. In a scientific context, deterministic behavior is important for ensuring that reported performance metrics can be reproduced exactly by independent groups. When a paper’s central claims depend on an ML model, documenting the random seed and software versions is a widely expected minimal standard. Without determinism, discrepancies between reproductions can be dismissed as training randomness rather than substantive methodological differences, weakening falsifiability. The paper does not provide evidence that training was controlled to be deterministic. This gap is amplified by the “download from latest release” instruction, which can introduce additional non-determinism via changing data artifacts.\n```c\n#include <emmintrin.h>\n```\nThis include indicates dependence on x86 SIMD intrinsics (SSE2), which can prevent compilation on non-x86 architectures without conditional compilation or alternative implementations. As a result, a reader’s ability to reproduce results may depend on having access to a compatible x86 environment, even though the paper does not state such a constraint. When core executables cannot be built, the pipeline cannot be executed end-to-end from BAM/CRAM as claimed, blocking reproduction of even basic demo runs. In modern genomics practice, ARM-based developer machines and some cloud environments are increasingly common, so portability affects practical reproducibility for a broad segment of users. Providing a Docker/Singularity image that demonstrably builds and runs (or providing portable SIMD alternatives) is standard for reducing this friction. The paper does not present such validated, architecture-agnostic reproducibility support in the manuscript.\n\nReferences:\n[4] [scikit-learn documentation: `sklearn.ensemble.RandomForestClassifier` (accessed 2026-02-20)](https://scikit-learn.org/stable/modules/generated/sklearn.ensemble.RandomForestClassifier.html)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|74|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb74", "comment": "The paper formally defines \"Hidden Split Reads\" (HSR) based on an alignment score improvement criterion, but the provided code implements read selection using a simple heuristic based on the number of mismatches and indels.\n\n\"Given a read $r[1..n]$, we say that $r$ is a hidden split read if there exists $i \\in [1..n-1]$ such that $score(r) < score(r[1..i]) + score(r[i+1..n])$; in other words, if $r$ is allowed to split into two without penalty and the two parts can align independently, the score of the alignment will increase.\"\nThis defines HSRs based on a rigorous comparison of alignment scores.\n\"In order to maintain a high precision, our algorithm only considers HSRs that have at least three differences with the reference genome ... Let us call such HSRs as strong HSRs.\"\nThis implies that the algorithm first identifies HSRs based on the definition and then filters them.\n```cpp\nbool is_hidden_split_read(bam1_t* r) {\n    if (is_left_clipped(r, config.min_clip_len) || is_right_clipped(r, config.min_clip_len)) return false;\n\n    int mismatches = bam_aux2i(bam_aux_get(r, \"NM\"));\n    // ... (calculation of indels) ...\n    return (mismatches + indels >= config.min_diff_hsr);\n}\n```\nThe implementation in `reads_categorizer.cpp` selects reads solely based on whether the sum of mismatches and indels exceeds a threshold (`min_diff_hsr`, default 3). It does not check the split alignment score condition for individual reads as defined in the paper. This heuristic approach may miss \"weak\" HSRs that satisfy the score definition but have fewer than 3 differences, and it conflates the definition of HSR with the \"strong HSR\" filter.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|74|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb74", "comment": "The validation of the generated 1000 Genomes Project catalogue relies on the 34 HGSVC2 samples, which were also used to train the SurVIndel2 model. This introduces bias when comparing against the 1000g-SV catalogue, which was generated using unsupervised methods.\n\n\"The machine learning model of SurVIndel2 was trained using the 34 samples in HGSVC2 sampled by the NYGC.\"\nThe 34 samples serve as the training set for the supervised model.\n\"We used SurVIndel2 to generate a catalogue of deletions and tandem duplications for 3,202 samples from the 1000g genomes project sequenced by the NYGC. SurVIndel2 was run on each individual sample\"\nThe catalogue includes the 34 training samples. Even if leave-one-out cross-validation was used for these 34 samples (which is not explicitly stated for the catalogue generation step, only for the benchmark), the validation metrics are derived from the same dataset distribution used for training.\n\"SurVIndel2 predicts 130,657 deletions not present in 1000g-SV, with high validation rate (0.87). ... SurVIndel2 also predicts 197,008 duplications that are not present in 1000g-SV, with high validation rate (0.85).\"\nThese validation rates are calculated using the 34 HGSVC2 samples. Extrapolating these high rates to the entire catalogue of 3,202 samples is problematic because the model is optimized for the specific characteristics of the HGSVC2 dataset. The 1000g-SV catalogue, generated by unsupervised callers like Manta [1], does not benefit from such supervised training on the test distribution, making the comparison unfair.\n\nReferences:\n[1] Chen, X. et al. (2016) Manta: rapid detection of structural variants and indels for germline and cancer sequencing applications. Bioinformatics, 32(8), 1220-1222. https://doi.org/10.1093/bioinformatics/btv710", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|74|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb74", "comment": "The paper compares SurVIndel2, a supervised method trained on the HGSVC2 dataset, with unsupervised methods (Manta, Delly, Lumpy) on the same dataset. This comparison favors the supervised method as it can learn dataset-specific artifacts.\n\n\"The machine learning model of SurVIndel2 was trained using the 34 samples in HGSVC2 sampled by the NYGC. For this reason, when testing them, we use a leave-one-out strategy.\"\nWhile leave-one-out prevents direct training on the test sample, the model still learns the general characteristics and biases of the HGSVC2 dataset (sequenced by NYGC with NovaSeq 6000).\n\"SurVIndel2 outperforms the other methods in both deletions and duplications, often by a large margin\"\nThe superior performance of SurVIndel2 could be partly attributed to its ability to learn the specific noise profile of the NYGC sequencing data, which unsupervised methods like Manta [1], Delly [2], and Lumpy [3] cannot do. A more rigorous evaluation would test the model on a completely independent dataset from a different sequencing center or population that was not involved in the training process (e.g., a dataset not included in HGSVC2).\n\nReferences:\n[1] Chen, X. et al. (2016) Manta: rapid detection of structural variants and indels for germline and cancer sequencing applications. Bioinformatics, 32(8), 1220-1222. https://doi.org/10.1093/bioinformatics/btv710\n[2] Rausch, T. et al. (2012) DELLY: structural variant discovery by integrated paired-end and split-read analysis. Bioinformatics, 28(18), i333-i339. https://doi.org/10.1093/bioinformatics/bts378\n[3] Layer, R. M. et al. (2014) LUMPY: a probabilistic framework for structural variant discovery. Genome Biology, 15(6), R84. https://doi.org/10.1186/gb-2014-15-6-r84", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|74|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb74", "comment": "I see the authors use SurVClusterer to compare SVs from various callset, but the manuscript could be improved by more information on how exactly that is done, and how the precision and sensitivity are calculated based on that. Note that a commonly accepted method for comparing structural variant call sets is Truvari (https://github.com/ACEnglish/truvari). Can the authors confirm that they obtained similar results with their tool?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|74|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb74", "comment": "The y-axis in Figure 1c and 1d is unlabeled.", "reviewer_type": "human", "label": "error", "error_type": "Neglect", "label_origin": "expert+llm-filter"}
{"id": "prb|74|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb74", "comment": "Mostly out of curiosity and not crucial for this paper, I wondered if it is possible to train the filter module on a combination of different species and what the performance of such a mixed model would be compared to the species-specific filter.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|74|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb74", "comment": "Figure 2 shows that over 93% of the tandem duplications of HG002 are in repeat regions. It would be good to see a breakdown of the types of repeat regions in the bar chart.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|74|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb74", "comment": "In section 2.3, the manuscript stated that filtering was implemented by leave-1-out training for SurVIndel2, but methods of the 'pre-trained random forest' filtering are not provided. Please include further description.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|74|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb74", "comment": "In addition to revision 2, section 2.3 didn't include descriptions of how filtering was performed on CNV calls of benchmarking tools. For example, Manta ranks the quality of SV calls using QUAL score and FILTER tags, and the choice of filtering strategy can impact the benchmarking results, particularly sensitivity. Figure 4 was generated with one set of calls per sample per caller. Possibilities of alternative filtering strategies were not explored. I recommend including multiple filtering options in the benchmarking, such as different QUAL cutoffs per sample per caller, and plot curves of precision-recall in figure 4(a), 4(b), and 5(a).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|74|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb74", "comment": "HG002 is a great independent sample, which was not specifically trained on by SurVIndel2, for benchmarking purposes. However, the discussion only includes sensitivity, not precision. I strongly recommend including HG002 in Figure 4(a) and 4(b) as well.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|74|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb74", "comment": "Very importantly, in section 2.3, Delly, Lumpy, and Manta were selected as benchmarking tools according to reference [4]. However, in this benchmarking study, GRIDSS is another top-performing SV caller. I strongly recommend including benchmarking with GRIDSS2 + Purple (Cameron, D.L., Baber, J., Shale, C. et al. GRIDSS2: comprehensive characterization of somatic structural variation using single breakend variants and structural variant phasing. Genome Biol 22, 202 (2021). https://doi.org/10.1186/s13059-021-02423-x).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|74|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb74", "comment": "It's interesting to see that SurVIndel 1&2 are more sensitive than other callers with no HSR support. Section 2.7 discusses the reasons why these CNVs have a low level of evidence. It would be good to include more discussion on why SurVIndel2 can capture more such CNVs than other callers, as well as the true positive rate of unsupported CNVs called by SurVIndel2.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|74|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb74", "comment": "I recommend including a discussion on the limitations of the tool regarding the detection of somatic CNVs in cancer genomes. This discussion could acknowledge that, unlike the other tools benchmarked in the study, SurVIndel2 does not currently support the identification of somatic CNVs, whichare critical for understanding cancer genomics. Highlight this as a significant caveat, and suggest future research directions or potential updates to the tool that could address this gap. Emphasize the importance of this functionality for comprehensive cancer genomics studies and how its inclusion could further elevate the tool's applicability and utility in the field. This addition will not only provide a more balanced view of SurVIndel2's capabilities but also align expectations for researchers interested in cancer genomics.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|74|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb74", "comment": "Throughout the manuscript, it seems the authors have considered all deletion (>= 50bp) and tandem duplication type SVs as CNVs. There is confusion as all deletions (>=50bp) can not be called CNV. Is the tool designed to detect all DEL and DUP-type SVs? If that is the case, then it is not suggested to call it a CNV caller tool.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|74|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb74", "comment": "The “Method” section is included inside the “Result” section. Also, that section only talks about the algorithms and techniques used in this tool. It would be better to include the benchmarking strategies such as what comparison tools and the truth set are used for evaluation. The results can be reproduced for verification if the VCF file for the truth sets, callsets, commands, or scripts are available in the “Methods” section. The authors could provide a link (e.g. GitHub repo) with all the result files.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|74|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb74", "comment": "The authors have used the HGSVC2 callsets as truth sets, so it is not clear if only DEL and DUP type SVs or the whole SV set is selected for the evaluations. Are these high-confidence call sets? Are they validated against GIAB truth sets? For each sample, the evaluation was performed using a training module of SurVIndel which was trained by using the features of other 33 long-read-based CNV callsets. So would it be also possible to compare the results of SurVIndel2 without using the last step to make a fair comparison with “pure” short-read-based callers? The evidence and claims can be better examined with the availability of callsets. Another suggestion is to use the GIAB SV truth set (v0.6) can also be used for the evaluation. The DEL-type SVs with length >=1kbp can be used as a benchmark set while evaluating all the callers. Also, why the precision is not computed for DEL types (last line of 1st paragraph of Section 2.3)?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|74|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb74", "comment": "The authors used the terms like “tandem repetitive regions”, and “repetitive regions” throughout the manuscript. It would be better if they are mentioned or a BED file is provided to identify those regions in reference. Are they telomere or centromere regions? It is difficult to understand the CNVs outside repetitive regions if they are not clearly defined or explained. Also, it is better to use the length information while using “shorter” terms for CNVs.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|75|Claude|1", "source": "prb", "split": "test", "paper_id": "prb75", "comment": "The paper claims to establish the MAGE-A4 TCB as \"highly specific\" and suitable for clinical development, yet the tissue screening is limited to only three organ types (liver, lung, colon), excluding critical tissues where fatal off-target toxicities have occurred in TCR-based therapies (e.g., heart). Given the well-documented fatal cardiac toxicity from cross-reactivity in MAGE-A3 TCR therapy with titin, the absence of cardiac tissue testing is a significant omission for a de-risking framework.\n\n\"We conclude that MAGE-A4 TCB is a highly specific, novel therapeutic engager molecule, with no observed off-target activity in liver, lung and colon tissues.\"\nThis conclusion is drawn from testing only three tissue types. The claim of being \"highly specific\" is overstated given the limited tissue panel. For a therapeutic platform intended to de-risk molecules \"prior to first-in-human clinical application,\" excluding major organs like heart, brain, kidney, and bone marrow leaves critical safety gaps. The HLA Ligand Atlas demonstrates substantial immunopeptidome diversity across tissues, with some tissues (e.g., thymus, spleen, bone marrow, kidney) having dramatically different peptide repertoires from those tested in this study [[1]](#citation-1).\n\"We further determine 16 cross-reactive sequences for ESK1, a TCR-like bispecific antibody recognizing WT-1 with known off-target activity, in healthy liver tissue.\"\nThis demonstrates the assay can detect off-targets when present. However, the same level of rigor is not applied to the novel MAGE-A4 TCB—only three tissues were tested before concluding the molecule is safe for clinical development. This asymmetric validation creates uncertainty about whether off-targets might exist in untested tissues.\n\"a T-cell receptor (TCR) against another MAGE-A3 peptide cross-reacted to a structurally similar Titin peptide in heart muscle cardiomyocytes, resulting in fatal cardiac toxicity\" [[2]](#citation-2)\nThis historical example from the closely related MAGE-A3 TCR therapy directly demonstrates the danger of cardiac cross-reactivity with MAGE family antigens. The titin cross-reactivity that caused patient deaths was not detected by typical preclinical screening strategies at the time, underscoring the importance of comprehensive tissue testing. The current paper's omission of cardiac tissue testing for the MAGE-A4 TCB is particularly concerning given this precedent.\n\nReferences:\n[1] Schuster, H., et al. (2021). \"HLA Ligand Atlas: a benign reference of HLA-presented peptides to enable T-cell based immunotherapy.\" *Journal for ImmunoTherapy of Cancer*, 9(4), e002071. https://jitc.bmj.com/content/9/4/e002071\n[2] Holland, C.J., et al. (2022). \"Structural insights into engineering a T-cell receptor targeting MAGE-A10.\" *Journal for ImmunoTherapy of Cancer*, 10(7), e004600. https://jitc.bmj.com/content/10/7/e004600", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|75|Claude|2", "source": "prb", "split": "test", "paper_id": "prb75", "comment": "The paper identifies 16 ESK1 off-target peptides in liver tissue, but none overlap with the 27 peptides previously identified by Gejman et al. (2020) using the PresentER platform. While the authors present this as discovering \"novel\" off-targets, the complete absence of overlap between two methods designed to find the same off-targets raises concerns about whether each method captures the complete interactome or whether tissue-specific factors and methodological differences create significant blind spots.\n\n\"Nine out of the 27 Gejman et al. 2020 reported peptides are known to be expressed in liver (Supplementary Table S1), however, none of the sequences were confirmed in our assays as physiological ligands presented by HLA in healthy (non-cancerous) human liver tissue (Figure 2D).\"\nThe authors acknowledge that 9 of 27 Gejman peptides should be expressed in liver tissue, yet none were detected by their immunoprecipitation-MS approach. This discrepancy could indicate that either (1) predicted expression does not translate to HLA presentation, (2) the MS-based assay lacks sensitivity for some peptides, or (3) both methods have systematic biases that result in complementary but incomplete coverage. Without understanding why these expected peptides were missed, the claim that the new method comprehensively identifies off-targets cannot be verified.\n\"Neither of these peptide candidates had been previously identified as an off-target candidate for ESK1, despite the fact that amino acid motifs for off-target sequences identified between our study and Gejman et al. 2020 show a remarkable similarity\"\nThe similar binding motifs but completely different peptide sequences suggest both methods tap into valid aspects of ESK1 recognition but identify non-overlapping portions of the interactome. For a de-risking strategy, this implies that neither method alone provides complete coverage, yet the paper does not recommend combining approaches or acknowledge this fundamental limitation when claiming suitability for clinical de-risking.\n\"a genetic minigene platform (PresentER) was used to experimentally test predicted peptide sequences for interaction with ESK1. Authors identified 100 peptide sequences to be interacting with ESK1, of which 27 entered validation assays\" [[3]](#citation-3)\nThe PresentER platform identified substantially more candidate sequences (100) than the immunopeptidomics approach presented here (16), though both interrogate ESK1 binding. The different yields and zero overlap suggest fundamentally different coverage patterns. For comprehensive safety assessment, complementary approaches may be necessary—a consideration not explicitly addressed in the proposed de-risking framework.\n\nReferences:\n[3] Gejman, R.S., et al. (2020). \"Identification of the Targets of T-cell Receptor Therapeutic Agents and Cells by Use of a High-Throughput Genetic Platform.\" *Cancer Immunology Research*, 8(5), 672-684. https://pubmed.ncbi.nlm.nih.gov/32184297/", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|75|Claude|3", "source": "prb", "split": "test", "paper_id": "prb75", "comment": "The authors explicitly state that no statistical method was used to predetermine sample size, with replicates chosen based on \"material availability and feasibility\" rather than statistical power considerations. For healthy tissue analysis, liver experiments used tissue from a single unspecified number of donors with 3 replicates, while functional killing assays used only 2 donors. Given the well-documented inter-individual variability in immunopeptidome composition, this limited sampling provides insufficient confidence for clinical de-risking conclusions.\n\n\"No statistical method was used to predetermine sample size, and the number of replicates was chosen on the basis of material availability and feasibility. However, three replicate analyses were considered a minimum requirement.\"\nFor a platform proposed to de-risk therapeutics \"prior to first-in-human clinical application,\" the lack of statistical power calculations is concerning. The determination that three replicates constitute a \"minimum requirement\" appears arbitrary rather than based on the known variability in immunopeptidomics data. This approach may be acceptable for proof-of-concept studies but falls short of the rigor expected for safety-critical assessments informing clinical decisions.\n\"Each graph represents two independent experiments with two independent human donors in quadruplicates\" (Figure 3D legend, liver spheroids) and \"Each graph represents two independent experiments with two independent human donors in triplicates\" (Figure 5 legend)\nTwo donors per tissue type provides minimal statistical power to account for inter-individual variability. The HLA Ligand Atlas demonstrates that \"even on the source protein level there is a higher similarity between samples that originate from the same subject over samples that originate from the same tissues,\" indicating substantial inter-individual heterogeneity in immunopeptidome composition [[1]](#citation-1). Testing only 2 donors risks missing off-targets present in the broader population.\n\"The interindividual heterogeneity outweighs similarities between tissue types... We assessed the similarity of the immunopeptidome on both source protein and HLA-ligand level between samples... and clustered the samples based on their similarity\" [[1]](#citation-1)\nThis finding from a comprehensive immunopeptidomics atlas directly contradicts the assumption that 2-3 donors can adequately represent population-level off-target risks. The documented inter-individual heterogeneity suggests that negative findings from limited donors cannot confidently rule out off-target binding in the broader HLA-A*02:01 positive patient population.\n\nReferences:\n[1] Schuster, H., et al. (2021). \"HLA Ligand Atlas: a benign reference of HLA-presented peptides to enable T-cell based immunotherapy.\" *Journal for ImmunoTherapy of Cancer*, 9(4), e002071. https://jitc.bmj.com/content/9/4/e002071", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|75|Claude|4", "source": "prb", "split": "test", "paper_id": "prb75", "comment": "Only 8 out of 16 ESK1-enriched peptides (50%) demonstrated T cell activation in the JNFAT assay. The authors characterize this as demonstrating the \"high specificity of the approach,\" but a 50% validation rate could equally be interpreted as a 50% false positive rate in the interactome identification. Furthermore, no correlation was observed between enrichment ratio and functional T cell activation, undermining the quantitative interpretation of the interactome data.\n\n\"We observe strong, off-target-induced T cell activation for 8/16 sequences, demonstrating the high specificity of the approach.\"\nCharacterizing a 50% validation rate as \"high specificity\" is questionable. While the authors correctly note that 8 of 16 peptides induced T cell activation, this also means 8 of 16 (50%) did not. If the goal is to identify functionally relevant off-targets for safety assessment, a method with 50% false positives requires substantial secondary validation, which somewhat undermines claims of an efficient de-risking platform.\n\"No correlation could be observed between the detected ESK1 HLAp enrichment ratio and the measured maximal RLU in a Jurkat reporter assay using peptide-pulsed T2 cells in the presence of ESK1\" (Supplementary Figure 3 legend)\nThe lack of correlation between enrichment intensity and functional activation is problematic for using enrichment ratios as a prioritization metric. The most enriched peptide (CRYL1, 256-fold enrichment) showed T cell activation, but SHC1 with only 5.3-fold enrichment showed the highest activation response. This dissociation between binding enrichment and functional activity limits the ability to prioritize candidates based on interactome data alone and necessitates comprehensive functional validation of all enriched sequences.\n\"the most significantly enriched peptides in the interactome assay, with high enrichment ratios. In depth analysis of the structure of the highest reactive peptide, SHC1_{469-477} (RVPPPPPQSV), did not immediately conclude why the peptide is significantly more active than the RMF target sequence\"\nThe authors acknowledge being unable to explain why SHC1 with relatively low enrichment (5.3-fold) showed the highest T cell activation while more highly enriched peptides were less active. This unpredictability in relating binding to function further emphasizes that the interactome assay alone cannot assess clinical safety risk without comprehensive functional follow-up.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|75|Claude|5", "source": "prb", "split": "test", "paper_id": "prb75", "comment": "The entire study focuses exclusively on HLA-A*02:01, yet patients expressing this allele typically also express five other HLA class I molecules that could present different peptide repertoires. The framework does not address how cross-reactivity mediated through other HLA alleles would be detected, limiting its applicability as a comprehensive de-risking strategy.\n\n\"An experimental framework de novo identifies on-target binding of the novel, functional MAGE-A4-specific TCB recognizing the peptide GYVDGREHTV presented by HLA-A*02:01\"\nThe MAGE-A4 TCB specifically targets HLA-A*02:01, so this restriction is appropriate for on-target validation. However, if off-target binding occurs through peptides presented by other HLA alleles present in patients, these would not be detected by this framework. The authors do not discuss this limitation or how their approach could be extended to evaluate potential off-targets presented by non-A*02:01 alleles.\n\"the strict human specificity of the HLA-I molecules, together with the limited overlap in protein processing and resulting peptide repertoires between humans and other species, invalidates the conventional toxicity testing in animals\"\nThe authors correctly identify HLA-specificity as a challenge for conventional toxicology but do not fully address the multi-allelic nature of human HLA expression. Each patient expresses up to six different HLA class I alleles, and the peptide repertoires presented by different alleles are largely distinct. A TCR-like antibody that binds peptides from multiple HLA alleles would require testing against each relevant allele's immunopeptidome.\n\"HLA variants that differ in peptide-contacting residues differ in the repertoire of peptides they present. The diversity of HLA alleles in the population is an important evolutionary mechanism for defense against diverse pathogens\" [[4]](#citation-4)\nThis established principle indicates that different HLA alleles present different peptide repertoires. While HLA-A*02:01 is the most common HLA-A allele in many populations (frequency ~25-50%), the framework would need adaptation to address therapeutic candidates targeting other HLA alleles or to comprehensively screen for cross-reactivity in patients with diverse HLA genotypes.\n\nReferences:\n[4] Abelin, J.G., et al. (2017). \"Mass Spectrometry Profiling of HLA-Associated Peptidomes in Mono-allelic Cells Enables More Accurate Epitope Prediction.\" *Immunity*, 46(2), 315-326. https://pmc.ncbi.nlm.nih.gov/articles/PMC5405381/", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|75|GPT|1", "source": "prb", "split": "test", "paper_id": "prb75", "comment": "This paper draws an overgeneralized conclusion that the novel MAGE-A4 TCR-like bispecific antibody has been de-risked and shows no off-target activity, even though the evidence only covers a narrow set of tissues/models and cannot support a first-in-human safety conclusion.\n\n\"Finally, we utilize our approach to de-risk our novel MAGE-A4 targeting TCR-like bispecific antibody prior to entering now ongoing clinical trials. We conclude that our strategy offers an accurate, scalable route for de-risking TCR-based therapeutics prior to first-in-human clinical application.\"\nThese sentences make a strong translational claim (“de-risk” before first-in-human) that goes beyond what the presented experiments can justify. The work demonstrates a tissue immunopeptidomics pull-down plus ex vivo killing readouts in a small number of selected models, which is helpful for hypothesis generation but not equivalent to comprehensive safety assessment. Because off-target toxicity can be driven by rare peptides, tissue- and donor-specific processing, and context-dependent HLA expression, negative findings in a limited panel do not imply absence of risk. In common preclinical practice for TCR/TCR-mimic modalities, multiple orthogonal screens are combined precisely because any single assay can miss relevant liabilities. The manuscript does not provide evidence that the specific tissues and donors tested are sufficient to support the stated breadth of the de-risking claim.\n\"We conclude that MAGE-A4 TCB is a highly specific, novel therapeutic engager molecule, with no observed off-target activity in liver, lung and colon tissues.\"\nThis conclusion is framed as a broad specificity statement, but it is only supported by experiments in three tissues and associated in vitro models described in the Results/Methods. The phrase “no observed off-target activity” is inherently limited by assay sensitivity and tissue/donor sampling, yet the manuscript presents it as a property of the molecule rather than a limitation of the screen performed. In mass-spectrometry-based immunopeptidomics, non-detection can reflect insufficient depth, ionization bias, peptide losses, or stochastic sampling, not true absence. For safety-facing claims, common practice is to explicitly bound conclusions to the tested tissues, donors, and detection limits, and to avoid implying global specificity. The manuscript’s wording risks readers interpreting limited negative results as robust evidence of clinical safety.\n\"Finally, in order to extend the functionality of our approach for de-risking of the novel MAGE-A4 TCB, we applied our interactome assay to two further healthy tissues from lung and colonic tissue. We used an isotype control targeting HLA-DQ, a low expressed HLA class II surface molecule. No peptides were significantly enriched by the MAGE-A4 IgG in these experiments (Figure 5A).\"\nThese sentences show that the “no off-target” conclusion is based on a very small extension to two additional tissues, rather than a systematic survey across a wider panel of organs and donors. For TCR-like therapeutics, clinically relevant off-targets can arise in unexpected tissues that were not pre-selected for screening, so tissue selection is a critical methodological design choice. Moreover, the observation “no peptides were significantly enriched” depends on statistical thresholds and proteomics depth, which are not equivalent to demonstrating that no relevant binders exist. In particular, enrichment-based workflows can miss off-targets that bind weakly yet still trigger T-cell activation when bridged to CD3, or bind to low-abundance peptides. Therefore, the experimental scope described here does not warrant the strength of the downstream clinical de-risking statement.\n\"The first two treated patients developed cardiogenic shock and died within a few days of T-cell infusion, events not predicted by preclinical studies of the high-affinity TCRs.\" [[4]](#ref4)\nThis sentence provides a concrete example from TCR-based therapeutics where severe off-target toxicity occurred despite substantial preclinical work, illustrating that negative preclinical findings do not guarantee safety. While the modality here is TCR-engineered T cells rather than a TCR-like bispecific antibody, the central risk mechanism—unexpected recognition of peptide–HLA complexes in essential tissues—overlaps. The implication for this manuscript is that claims of “de-risking prior to first-in-human” should be carefully bounded to what the assay panel can and cannot detect. The paper’s conclusion does not clearly communicate how residual risk remains, especially outside the tested tissues and donors. This gap matters because the manuscript positions the platform as an accuracy and safety-enabling strategy.\n\"Extensive preclinical investigations revealed no off-target antigen recognition concerns; nonetheless, administration to patients of T cells expressing the affinity-enhanced MAGE A3 TCR resulted in a serious adverse event (SAE) and fatal toxicity against cardiac tissue.\" [[3]](#ref3)\nThis sentence reinforces that off-target liabilities may evade preclinical screens, including those that appear extensive, which is directly relevant to how strongly the current manuscript should phrase its de-risking conclusion. The present study screens a limited set of tissues (liver, lung, colon) and uses enrichment plus ex vivo assays, but does not establish that these are sufficient to rule out clinically meaningful off-targets in other organs. The cited work also recommends additional strategies to mitigate risk, indicating that a single platform is unlikely to be definitive. Therefore, the manuscript’s framing of its approach as an “accurate” route for de-risking before first-in-human is not well supported by the scope of evidence. A more defensible conclusion would restrict claims to the tested contexts and emphasize integration with broader screening.\n\nReferences:\n[3] <a id=\"ref3\"></a> [Cameron BJ et al. Identification of a Titin-derived HLA-A1-presented peptide as a cross-reactive target for engineered MAGE A3-directed T cells. *Science Translational Medicine* (2013).](https://pubmed.ncbi.nlm.nih.gov/23926201/)\n[4] <a id=\"ref4\"></a> [Linette GP et al. Cardiovascular toxicity and titin cross-reactivity of affinity-enhanced T cells in myeloma and melanoma. *Blood* (2013).](https://pmc.ncbi.nlm.nih.gov/articles/PMC3743463/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|75|GPT|2", "source": "prb", "split": "test", "paper_id": "prb75", "comment": "This paper uses a control strategy for immunopeptidomics enrichment that can create false negatives for off-target discovery—by treating another peptide–HLA-binding therapeutic (ESK1) as an “isotype control” for MAGE-A4 (and vice versa)—which undermines the validity of its interactome comparisons and the specificity claim for MAGE-A4.\n\n\"We chose to perform a “head to head” immune-enrichment from primary liver tissue resections using both, MAGE-A4 and ESK1 IgGs. Since both target antigens MAGE-A4 WT-1 are not expressed in A375 cells (data not shown), the ESK1 enrichment could serve as isotype control for the MAGE-A4 IgG, and vice versa.\"\nIn enrichment-based immunopeptidomics, a key control objective is to estimate non-specific carryover from beads, resin, and sample handling using a reagent that does not share the specific binding mechanism under study. Here, the “control” is another pMHC-binding antibody with its own specificity and cross-reactivity profile, which is not equivalent to an isotype that lacks pMHC specificity. If both molecules bind the same off-target peptide–HLA complex (or share background interactions), a differential “head-to-head” comparison can subtract the shared signal and cause those ligands to be missed. This design choice is especially problematic given the manuscript’s emphasis on de novo off-target discovery and the later claim of “no observed off-target activity” for MAGE-A4. The paper does not provide an analysis showing that shared binders are unlikely or that an orthogonal negative control yields the same MAGE-A4 conclusion.\n\"The comparison of significantly enriched interactomes for both antibodies uncovered 16 HLA-A*02:01 peptides for Esk1, and 1 peptide for the MAGE-A4 TCB (Figure 2A, Table 1).\"\nThis sentence shows that the core discovery result depends on comparing two antibody pulldowns against each other rather than comparing each pulldown against a truly irrelevant antibody pulldown from the same tissue. Because the output is framed as what is “significantly enriched” in one relative to the other, any peptide–HLA complex enriched by both will not appear as specific to either and can be dropped from interpretation. That creates a systematic blind spot precisely for “shared off-targets,” which are clinically important because they can still drive toxicity even if not unique to one molecule. The manuscript then uses the small number of MAGE-A4-enriched peptides to support a high-specificity conclusion, but the comparison method itself could constrain that number. Without demonstrating robustness to alternative controls, this finding is not strong enough to support the specificity claim.\n\"Lysates were pre-cleared with 1.5 ml of Protein A/G-bead mixture, and then incubated with antibody beads for at least 5 h at 4°C with gentle rotation. Peptides were eluted from the captured HLA-complexes by addition of 1.5 ml of 10% acetic acid and dried by vacuum centrifugation.\"\nThese steps illustrate that the assay output is inherently a mixture of specific capture and non-specific adsorption effects that depend on resin, antibody immobilization chemistry, tissue lysate composition, and washing conditions. In this context, control selection strongly influences which peptides are interpreted as “specific” binders, because different antibodies can differ in non-specific stickiness and in their own true binding. Using another specific pMHC binder as the comparator conflates specificity with relative enrichment between two biological binders, rather than isolating non-specific background. This matters most for claims about absence of MAGE-A4 off-targets, where false negatives are more harmful than false positives. The manuscript does not provide evidence (e.g., parallel irrelevant-IgG controls for the liver head-to-head experiment) that the background and shared-binding problem is negligible.\n\"Appropriate controls need to be chosen depending on the experiment; for example, for infected or tumor cells, respective healthy cells need to be used, and for HLA or antigen-transfected antigen-presenting cells (APCs), the untransfected parental cell line, or cells containing irrelevant HLA should be used.\" [[1]](#ref1)\nThis guidance from a widely used immunopeptidomics protocol emphasizes that control choices should isolate the variable of interest by using truly “irrelevant” comparators. Although the context here is cell-state and HLA/antigen transfection controls, the underlying principle applies directly to antibody-enrichment immunopeptidomics: controls should not introduce a competing specific binding phenotype. The reviewed manuscript’s head-to-head design violates this principle by comparing two therapeutics that both can bind peptide–HLA complexes in a tissue lysate. That makes it hard to interpret a low number of MAGE-A4-enriched ligands as evidence of high specificity rather than an artifact of the comparison baseline. The discrepancy between common control recommendations and the manuscript’s design weakens confidence in negative off-target findings. This is a methodological issue that materially affects the validity of the paper’s conclusions.\n\nReferences:\n[1] <a id=\"ref1\"></a> [Purcell AW, Ramarathinam SH, Ternette N. Mass spectrometry–based identification of MHC-bound peptides for immunopeptidomics. *Nature Protocols* (2019).](https://researchmgt.monash.edu/ws/portalfiles/portal/275054035/275053880_oa.pdf)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|75|GPT|3", "source": "prb", "split": "test", "paper_id": "prb75", "comment": "This paper claims that the identified off-target peptide–HLA ligands are causally responsible for ESK1-induced killing in a liver spheroid system, but the experiments do not establish that the same ligands are endogenously presented in the killing model or that they drive the observed cytotoxicity, making the causal conclusion insufficiently supported.\n\n\"We finally confirm that the observed cross-reactivities lead to killing in 3D healthy human liver cells in co-culture with ESK1 and PBMC, confirming the validity of our assay and causality of the detected cross-reactive HLAp sequences.\"\nThe manuscript explicitly claims “causality” between specific detected peptide–HLA ligands and observed killing, which is a high bar for evidence. Demonstrating that ESK1 kills liver spheroids shows that some on- or off-target ligand(s) exist in that model, but it does not identify which endogenous peptide–HLA complexes are responsible. The paper does not show an immunopeptidomics readout from the spheroid system itself that confirms presentation of the same 16 (or the 8 active) ligands under the assay conditions. Nor does it use perturbations (e.g., source-protein knockout/knockdown, peptide competition, HLA blocking at the relevant allele, or rescue) to link specific peptides to killing. Without such linkage, the killing result supports “ESK1 has physiologically relevant off-target activity in a liver model” but not the claimed peptide-level causality.\n\"The 16 peptides enriched by the ESK1 IgG were evaluated for their potential recognition by ESK1 TCB using Jurkat NFAT activation assay. T2 cells were first pulsed with the peptides and then co-incubated with JNFAT effector cells in the presence of different concentrations of ESK1 TCB.\"\nThis experiment evaluates whether ESK1 can respond to candidate peptides when artificially loaded onto a model cell line, which is a useful functional filter but not direct evidence about endogenous presentation in liver spheroids. Peptide pulsing bypasses antigen processing and can drive supraphysiological peptide–HLA densities that may not occur in primary tissues. As a result, a peptide that activates Jurkat cells when pulsed could still be irrelevant in vivo if it is not naturally presented (or not presented at sufficient density) in the target tissue model. Conversely, endogenous toxic ligands might not be included among the tested peptides, especially if enrichment/identification misses them. Therefore, these data support “ESK1 can recognize these sequences” but do not establish that these sequences are the causal drivers of the spheroid killing phenotype.\n\"T2 cells were pulsed with peptides (cells were incubated in 1 ml media at a density of 1 mio/ml in IMDM 10 % FCS in the presence of 1x10-4M – 1x10-9M POTP or control RMF peptide for 2 hrs at 37°C and washed with IMDM 10% FCS).\"\nThis protocol indicates peptide pulsing up to 10^-4 M (100 µM), which is far above the low-nanomolar peptide concentrations often used when trying to approximate physiological epitope densities on target cells. Such high pulsing can saturate surface HLA-A*02:01 and create activation signals that are not representative of endogenous antigen presentation levels in tissues. This inflates the risk that “potent activation” is an artifact of peptide loading rather than a realistic risk antigen in situ. Because the paper then interprets these activation data alongside tissue enrichment as evidence of physiologically relevant toxicity mechanisms, the use of very high peptide doses weakens the strength of causal inference. A more causal design would quantify endogenous copies-per-cell of the implicated ligands in the relevant liver model and demonstrate activation/killing at those densities.\n\"Peptide pulsing is routinely performed using peptide concentrations in the micromolar range. However, on the basis of the data presented here, such high concentrations are associated with the risk of producing T2 cells that present an unnaturally elevated number of epitopes. In turn this not only may result in an inaccurate assessment of T-cell sensitivity to naturally presented TAAs, but also may give false indications on the suitability of specific T cells or TCRs for immunotherapeutic applications.\" [[5]](#ref5)\nThis statement directly cautions that micromolar peptide pulsing can yield non-physiological epitope densities and misleading functional conclusions, which is relevant to the reviewed paper’s Jurkat/T2 validation strategy. Because the manuscript uses peptide-pulsed T2 cells to infer which enriched sequences are likely to be dangerous off-targets, the risk of “false indications” is directly applicable. The reviewed paper’s pulsing range reaches 100 µM, which falls squarely into (and beyond) the regime warned about in this external work. That means the observed Jurkat activation ranking may not reflect what would happen at endogenous ligand densities in human tissues. Therefore, the manuscript’s claim of peptide-level causality and “potent” off-target risk is not adequately supported by this assay design alone. Additional endogenous-presentation validation would be needed to justify the strength of the causal statements.\n\"Our findings indicate that peptide concentrations in the low nanomolar range are required for T2 cells to present TAAs in extents that are comparable to those of malignant cells.\" [[5]](#ref5)\nThis sentence provides a quantitative benchmark for using T2 peptide pulsing to approximate physiological epitope densities: low nanomolar concentrations. In contrast, the reviewed manuscript uses peptide pulsing conditions spanning into micromolar and higher concentrations, which can push presentation far beyond natural levels. If the goal is to infer physiological off-target risk, functional validation ideally operates near the ligand densities expected in tissues, not at saturating levels. The mismatch between recommended concentration regimes and the reviewed paper’s pulsing protocol makes it difficult to interpret activation as evidence of in situ potency. This further undermines the manuscript’s claim that its functional assays establish causality of the specific identified ligands in a physiological context.\n\nReferences:\n[5] <a id=\"ref5\"></a> [Bossi G et al. Examining the presentation of tumor-associated antigens on peptide-pulsed T2 cells. *OncoImmunology* (2013).](https://pmc.ncbi.nlm.nih.gov/articles/PMC3894244/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|75|GPT|4", "source": "prb", "split": "test", "paper_id": "prb75", "comment": "This paper’s identification of “significantly enriched” interactome peptides relies on statistical procedures that are not described with sufficient rigor for high-dimensional proteomics and appear to lack multiple-hypothesis control, threatening the validity of the reported peptide lists and downstream motif/structure conclusions.\n\n\"Significant changes between samples and in peptide abundance were calculated using the inbuild PCA and Anova evaluation in Progenesis.\"\nThis sentence indicates that differential peptide abundance (the core driver of “significant enrichment”) is computed with an ANOVA-based workflow inside Progenesis, but it does not specify crucial details needed to assess statistical validity. In immunopeptidomics, thousands of peptides are typically tested, so unadjusted ANOVA p-values can generate substantial false positives unless multiple testing correction is applied. The manuscript does not state whether p-values were adjusted (e.g., Benjamini–Hochberg) or how missingness and peptide-level aggregation were handled, both of which materially affect peptide-level significance. Because the paper’s claims about discovered interactomes and motifs depend on which peptides cross “significance” thresholds, lack of clarity here threatens the reliability of the main results. Reporting adjusted significance and clearly defined thresholds is standard practice in quantitative omics analyses.\n\"A score cutoff of -10lgP=20 was chosen to result in an acceptable false discovery rate (FDR) below 5.5%.\"\nThis sentence sets the peptide identification stringency for the entire discovery pipeline, and the chosen FDR is relatively permissive for a setting where individual peptide sequences are treated as potential safety-relevant off-targets. Even a modest false identification rate can contaminate a small list of “de novo” off-target candidates, especially when downstream structural modeling and motif claims are derived from those sequences. The manuscript also does not clarify whether this FDR applies at the PSM, peptide, or protein level, which affects how many incorrect peptide sequences may enter the list. In safety-focused discovery, common practice is to use stringent identification criteria and/or validate key peptides with synthetic standards and spectrum matching to avoid basing conclusions on misassignments. The paper does not provide such MS-level validation for the newly proposed off-target ligands.\n\"The comparison of significantly enriched interactomes for both antibodies uncovered 16 HLA-A*02:01 peptides for Esk1, and 1 peptide for the MAGE-A4 TCB (Figure 2A, Table 1).\"\nThis result depends directly on which peptides are deemed “significantly enriched,” making the statistical pipeline central to the paper’s primary claim of de novo interactome definition. Without explicit multiple-testing control and transparent criteria, it is difficult to determine whether the 16-peptide list is stable under reasonable analytical choices or whether it includes a non-trivial fraction of false discoveries. The manuscript also uses enrichment significance to justify downstream generalizations (e.g., motif preferences, structural compensation motifs), so statistical instability would propagate into mechanistic interpretation. In high-dimensional LC–MS datasets, it is common to provide adjusted p-values/q-values and to show robustness across replicates/donors and analysis settings. The paper does not provide sufficient statistical reporting to support the level of confidence implied by this “uncovered 16” statement. This is a major concern because the paper positions the approach as “high specificity” off-target discovery.\n\"Significance values are false discovery rate (FDR) adjusted.\" [[6]](#ref6)\nThis sentence exemplifies a common best practice in immunopeptidomics-style quantitative analyses: reporting significance with FDR adjustment to account for multiple hypothesis testing. The reviewed manuscript, by contrast, describes using ANOVA and reports “significant enrichment” but does not state that significance values were FDR-adjusted at the peptide level. Because interactome discovery involves testing many peptides simultaneously, omitting multiplicity control can materially inflate the number of apparent “significant” hits. The external paper’s explicit reporting highlights that multiplicity adjustment is a standard expectation in comparable LC–MS quantitative settings. Therefore, the lack of comparable reporting in the reviewed manuscript weakens confidence in the claimed significance-driven discoveries.\n\nReferences:\n[6] <a id=\"ref6\"></a> [Stopfer LE et al. Multiplexed relative and absolute quantitative immunopeptidomics reveals MHC I repertoire alterations induced by CDK4/6 inhibition. *Nature Communications* (2020).](https://www.nature.com/articles/s41467-020-16588-9)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|75|GPT|5", "source": "prb", "split": "test", "paper_id": "prb75", "comment": "This paper does not provide public access to the underlying mass spectrometry data and analysis outputs needed to reproduce or audit the interactome discoveries, which substantially limits reproducibility and independent validation of safety-relevant off-target claims.\n\n\"All data will be made available to academic researchers upon reasonable request.\"\nFor discovery proteomics (including immunopeptidomics), community norms strongly favor deposition of raw MS data and identification results in established repositories, enabling independent reprocessing and verification. A “reasonable request” policy makes it difficult to assess the robustness of peptide identifications, enrichment statistics, and potential alternative explanations, and it can impede timely replication by other groups. This is particularly problematic here because the central claims identify specific off-target peptide sequences with direct implications for therapeutic safety. Without public access, other researchers cannot confirm spectral quality, assess FDR control, or test whether different search engines/parameters recover the same peptides. As a result, the paper’s key discoveries are not readily auditable, which undermines confidence in claims positioned as a preclinical de-risking strategy.\n\"Raw data files were analysed in Progenesis (Nonlinear Dynamics, Waters), and spectral identification was performed with PEAKS X software (Bioinformatic Solutions) using a protein sequence fasta file containing 20,397 reviewed human Uniprot entries downloaded on 04.03.2020.\"\nThis sentence indicates reliance on proprietary software pipelines for both quantification and identification, which increases the importance of sharing raw data and exportable results (e.g., peak lists, PSM tables, search parameters). Without access to the raw files and the full exported identification/quantification tables, independent groups cannot replicate the workflow, check parameter choices, or re-run searches with alternative tools. In addition, enrichment significance was calculated “in Progenesis,” so the exact statistical outputs and preprocessing steps become part of the essential methods needed for reproducibility. The manuscript does not provide a public repository with these artifacts, nor does it provide sufficient details to reconstruct them fully. This limits the paper’s utility as a general framework for de-risking across laboratories.\n\"Each submitted dataset to PX via PRIDE must contain: -­‐ peptide/protein identification files (called ‘RESULT’), -­‐ mass spectrometer output files (called ‘RAW’), which are either machine raw files or not heavily processed files in a XML-­‐based format such as mzXML or mzML (3),\" [[2]](#ref2)\nThis guideline from ProteomeXchange/PRIDE describes a widely used community standard for sharing proteomics datasets, including the raw instrument output and the identification results required for reuse. The reviewed manuscript does not report a ProteomeXchange (PXD) accession or equivalent public deposition for its MS/MS immunopeptidomics datasets. Given that the paper’s main contributions depend on LC–MS/MS peptide identifications from tissue, adherence to these standards would allow others to validate the peptide lists and reanalyze with updated methods. The discrepancy between community submission expectations and the manuscript’s “upon request” policy represents a significant reproducibility gap. This is not a minor documentation issue; it directly affects whether the key safety-relevant claims can be independently audited.\n\"The mass spectrometry proteomics data have been deposited to the ProteomeXchange Consortium via the PRIDE partner repository with the data set identifier PXD017407.\" [[6]](#ref6)\nThis sentence provides an example of current field practice in immunopeptidomics-adjacent work: depositing MS data to ProteomeXchange/PRIDE with a dataset identifier. It demonstrates that public deposition is feasible and increasingly expected, especially for studies that make peptide-level claims. The reviewed manuscript’s decision not to provide an accession number (and instead offer data on request) therefore falls short of common reproducibility standards. Because interactome discovery is sensitive to search parameters and filtering, access to raw data is necessary to evaluate whether the conclusions hold under reanalysis. This external example strengthens the critique that the reviewed paper’s data availability policy is a major barrier to reproducibility.\n\nReferences:\n[2] <a id=\"ref2\"></a> [ProteomeXchange/PRIDE. Tutorial: Submission of MS/MS datasets to ProteomeXchange via PRIDE (Submission Tutorial v2.3.1, 31 July 2015).](https://www.proteomexchange.org/docs/Submission_Tutorial.pdf)\n[6] <a id=\"ref6\"></a> [Stopfer LE et al. Multiplexed relative and absolute quantitative immunopeptidomics reveals MHC I repertoire alterations induced by CDK4/6 inhibition. *Nature Communications* (2020).](https://www.nature.com/articles/s41467-020-16588-9)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|75|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb75", "comment": "The paper claims to provide a \"de-risking experimental framework\" but fails to demonstrate that the mass spectrometry (MS) method has sufficient sensitivity to detect low-abundance off-target peptides that are below the MS limit of detection (LOD) yet above the threshold for T cell activation.\n\n\"We first confirmed and quantified presentation of the MAGE-A4 target peptide sequence by HLA-A*02:01 on A375 cells using a standard, targeted immunopeptidomics approach, and determined the target peptide abundance to a minimum of 30-50 copies per cell in cells and xenografts\"\nThe authors quantify the *target* peptide, which is likely highly expressed, finding 30-50 copies. However, they do not determine the LOD for *off-target* peptides. T cells are known to be extremely sensitive, capable of responding to as few as 1-3 peptide-MHC complexes per cell [1]. If an off-target peptide is present at 5-10 copies per cell in a vital organ, it could trigger a lethal autoimmune response, yet it would likely be missed by the MS assay if the LOD is around 30-50 copies (or higher for non-targeted discovery).\n\"We did not observe a significant correlation between the measured fold enrichment and the degree of T cell activation (Supplementary figure S3).\"\nThis lack of correlation further suggests that MS abundance (enrichment) is not a reliable proxy for immunogenicity. A peptide with low enrichment (or below detection) could still be highly potent. Relying on MS detection as a primary safety filter is therefore risky without a complementary high-sensitivity screen.\n\"A single peptide-major histocompatibility complex ligand triggers digital cytokine secretion in CD4+ T cells\" [1]\nThis literature demonstrates the extreme sensitivity of T cells, highlighting the gap between MS detection limits and biological relevance.\n\nReferences:\n[1] Huang, J. et al. A single peptide-major histocompatibility complex ligand triggers digital cytokine secretion in CD4+ T cells. Immunity 39, 846-857 (2013). https://pubmed.ncbi.nlm.nih.gov/24210352/", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|75|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb75", "comment": "The paper dismisses the off-target peptides identified by Gejman et al. (2020) solely because they were not found in the liver tissue MS data, without adequately investigating whether this is due to true absence or method sensitivity/bias.\n\n\"Nine out of the 27 Gejman et al. 2020 reported peptides are known to be expressed in liver (Supplementary Table S1), however, none of the sequences were confirmed in our assays as physiological ligands presented by HLA in healthy (non-cancerous) human liver tissue\"\nThe authors note that the proteins are expressed in the liver, yet the peptides were not found. They conclude that Gejman's results are not \"physiological\". However, a more likely explanation for at least some of these could be the limited sensitivity of MS compared to the genetic library screen used by Gejman et al. [2]. The paper should have performed spiking experiments or targeted MS (PRM) for the Gejman peptides to confirm their absence, rather than assuming the MS discovery data is comprehensive.\n\"Identification of the Targets of T-cell Receptor Therapeutic Agents and Cells by Use of a High-Throughput Genetic Platform\" [2]\nGejman et al. identified these peptides using a method that is independent of tissue expression levels (PresentER). The complete lack of overlap suggests a significant blind spot in one or both methods. Simply discarding the previous findings as \"non-physiological\" without rigorous exclusion (e.g., proving they are not processed/presented even when the protein is expressed) is premature.\n\nReferences:\n[2] Gejman, R. S. et al. Identification of the Targets of T-cell Receptor Therapeutic Agents and Cells by Use of a High-Throughput Genetic Platform. Cancer Immunol Res 8, 672-684 (2020). https://pubmed.ncbi.nlm.nih.gov/32317292/", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|75|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb75", "comment": "The paper claims to establish a \"de-risking experimental framework\" but only tests a very small number of tissues (liver for ESK1; lung and intestine for MAGE-A4), which is insufficient to claim a therapeutic candidate is de-risked for clinical trials.\n\n\"Finally, we utilize our approach to de-risk our novel MAGE-A4 targeting TCR-like bispecific antibody prior to entering now ongoing clinical trials.\"\n\"De-risking\" a TCR-based therapeutic requires demonstrating a lack of cross-reactivity across a broad panel of essential organs (e.g., heart, brain, kidney, bone marrow), as off-target toxicity in any of these can be fatal [3]. Testing only lung and intestine, while useful, does not constitute a comprehensive de-risking package. The title and conclusions are therefore overstating the scope of the safety assessment provided by this framework.\n\"We chose to perform a “head to head” immune-enrichment from primary liver tissue resections using both, MAGE-A4 and ESK1 IgGs.\"\nFor ESK1, only liver tissue was tested. While liver is a known target for ESK1 toxicity, a general framework should propose a multi-tissue strategy. The limited scope questions the \"scalability\" and \"completeness\" of the proposed framework for general application.\n\nReferences:\n[3] Linette, G. P. et al. Cardiovascular toxicity and titin cross-reactivity of affinity-enhanced T cells in myeloma and melanoma. Blood 122, 863-871 (2013). https://pubmed.ncbi.nlm.nih.gov/23926307/", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|75|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb75", "comment": "The paper proposes a \"compensation binding motif\" and structural mimicry to explain off-target binding, but this is supported only by computational modeling without experimental structural validation (e.g., crystallography or mutagenesis).\n\n\"To explore how ESK1 might be able to bind to the off-target peptides... we generated a molecular model of all of the Jurkat-NFAT confirmed eight peptides... based on the X-ray crystal structure (PDB-ID: 4WUU)\"\nThe authors rely entirely on homology modeling to explain the binding. While plausible, molecular dynamics or docking simulations are not a substitute for experimental data.\n\"Residue G4 of the RMB4B_{59-67} (KLHGVNINV) peptide is able to substitute for P at position 4... and promotes a turn in the backbone.\"\nThis specific structural claim about the backbone turn is derived from the model. To rigorously support the \"mimicry\" conclusion, the authors should have performed mutagenesis on the antibody (e.g., mutating the residues predicted to interact with the \"mimic\" residues) or the peptide to confirm that binding is indeed driven by these specific interactions, or solved the crystal structure of the complex.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|75|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb75", "comment": "De novo identification of TCR-ligands is a major challenge in immunology and immunotherapy. Yet, the method described was not applied for TCRs but rather to TCR-like antibodies. It seems unlikely that the same approach can be used to identify TCR-ligands due to the low affinity of TCR-HLAp interactions. The method is therefore likely to be limited to identifying ligands for TCR-like antibodies, making the title misleading.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|75|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb75", "comment": "The results in Fig. 2A and 5A show that the number of peptides identified by the method can be very high. Yet, there is no information about reproducibility in the text or the figure legends. For Fig 5, there is also discrepancy between the main text and the figure legend explaining the use of an isotype-control (anti-HLA-DQ) or ESK1, respectively. The axes read “MAGE/CTRL”. Moreover, the authors explain that the intended target for the MAGE4-HLA-A2 antibody was the only peptide that was detected in two biological replicates. This indicates that there is considerable variation between results obtained in replicates.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|75|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb75", "comment": "The title suggests that the intention is to de-risk a candidate therapeutic. The question is therefore if the method can replace testing of T-cell reactivity. This would be an important achievement since testing T-cell reactivity against primary tissue is often not possible. However, to prove this, one would need more data. To start with I would suggest testing a panel of TCR-like antibodies with different reactivity against a panel of cell lines in cell-based activation assays. One can then determine to what extent IP-MS is predictive of reactivity in cell-based assays.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|75|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb75", "comment": "What is the % recovery of eluted peptides from the HLAs purified using the process developed by the authors? In order for their method to be widely applicable as a tool in drug development, this must be established first. While exhaustiveness seems nearly impossible to accomplish, some estimate of the % coverage of endogenous peptidomes should be provided.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|75|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb75", "comment": "In addition to the work by Gejman and colleagues that is extensively discussed and compared with the present work, previous platforms have been described to evaluate cross-reactivities between TCR-like molecules and pHLA antigens (see, for example Birnbaum et al., Cell 2014; Gee et al., Cell 2018; Kula et al., Cell, 2019). These methods claim some level of exhaustiveness in identifying pHLA antigens for specific TCRs, so it would be important to outlined how the current approach compares to these methods for a specific exemplar antigen.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|75|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb75", "comment": "How sensitive is the interaction between the S7D03 with pHLAs presenting MAGE-A4 on the HLA allotype? This should be explicitly addressed by evaluating cross-reactivities with other allotypes that can display the same peptide, either in vitro or even better in situ using the author’s novel technology.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|75|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb75", "comment": "The structural modeling and subsequent SASA/RMS analyses presented in Figure 4 and Table 2, respectively, as a rationale for the molecular basis of the identified cross-reactivities assumes that all peptides are presented in a very similar backbone conformation, and that binding of ESK1 doesn’t induce significant structural changes. For example, it is conceivable that peptides may adopt different backbone conformations presenting key hotspot residues in geometries which mimic the Ab-bound complex, or that the ESK1 CDRs undergo considerable structural adaptations to accommodate different antigens, in an induced-fit type mechanism. Both assumptions must be verified experimentally by the authors by determining the crystal structures of the pHLA/ESK1 complexes to adequately support their conclusions. In the absence of experimentally determined structures these conclusions are highly speculative.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|75|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb75", "comment": "The primary SPR data (sensograms) summarized in Supp. Table 1 should be also provided, including the fitted curves which were used to derive on and off rates.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|75|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb75", "comment": "Since the novelty of the work lies primarily in the immunopeptidomic analysis, the primary data should be made available in an existing data base or author-supplied web-page.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|75|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb75", "comment": "Figure 1D-F. The authors found that IP with Mage-A4 ab detects significant enrichment of the expected peptide compared to control IPs. Could the complete list of detected peptides be made available to readers? Are other peptides significantly enriched in at least one out of the two experiments?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|75|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb75", "comment": "Figure 2. The design of the experiment is quite confusing. The authors claim that “Since both target antigens MAGE-A4 WT-1 are not expressed in A375 cells (data not shown), the ESK1 enrichment could serve as isotype control for the MAGE-A4 IgG, and vice versa”. As used for previous experiments, A375 express MAGE-A4 IgG targets. To my knowledge, A375 cell line also express WT-1. in any case, it is difficult to understand why the expression of these antigens in the A375 line is a determining argument for the selection of control IPs made with liver tissue. The control IP should have been performed with an isotype control antibody.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|75|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb75", "comment": "Figure 3D. The authors claim that MAGE-A4 and WT-1 are not expressed by the liver spheroids used in the experiments. This aspect should be tested if it has not been evaluated in previous studies (cite as appropriate). The authors should display raw values rather that normalized values, to assess the background (generated by control TCB) of cell killing resulting from these experiments.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|75|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb75", "comment": "Figure 5A. What are the few hits that are enriched with MAGE-A4 IgG in the volcano plot Lung (tissue)? Although they are not HLA-A*20:01 bind peptides, they might constitute unrelated off-targets. As point out above, the authors should display raw values rather that normalized values, to assess the background (generated by control TCB) of cell killing resulting from these experiments (% of cells remaining compared to the starting number incubated for the assay).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|75|Human_3|8", "source": "prb", "split": "test", "paper_id": "prb75", "comment": "What is the threshold used to predict peptide binding with HLA-A*02:01, and what are the Score obtained with NetMHCpan-4.1 for each detected peptide?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|75|Human_3|11", "source": "prb", "split": "test", "paper_id": "prb75", "comment": "The legend of Figure 5A is incorrect", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|76|Claude|1", "source": "prb", "split": "test", "paper_id": "prb76", "comment": "The off-target safety validation for the PTPRZ1-reactive TCR is limited to in silico AI-based prediction (ARDitox) followed by testing only 12 predicted peptides, without performing established empirical screening methods such as combinatorial peptide library (CPL) scans or systematic amino acid substitution assays that are considered the field standard for comprehensive TCR cross-reactivity assessment.\n\n\"To experimentally assess potential off-targets, we applied ARDitox, an in silico artificial intelligence (AI)-based prediction tool for off-target TCR binding. A panel of potential off-targets for the PTPRZ1^{1814-1822} TCR was generated with various off-target-specific safety and presentation scores (Fig. 2E, Table S2). No high-risk (safety score < 3) potential off-targets were predicted while 12 low-risk (safety score > 3) off-targets with relevant presentation probabilities on HLA-A*02 were predicted. In a subsequent Jurkat reporter assay, we did not find reactivity against any of these 12 potential off-targets (Fig. 2F).\"\nThe authors rely exclusively on computational prediction to select which off-target peptides to test experimentally. This approach is fundamentally limited because in silico tools can only predict cross-reactivity based on sequence similarity, missing peptides with different sequences that may still be recognized due to structural mimicry. The MAGE-A3/Titin case demonstrates that cross-reactive peptides can share as few as 5 of 9 amino acids, making computational prediction alone insufficient.\n\"Together, these data reveal a patient-derived vaccine-induced PTPRZ1^{1814-1822}-reactive TCR that binds to both exogenous and intracellularly processed and presented antigen on MHC-I and does not react against AI-predicted low-risk off-targets.\"\nThe conclusion that the TCR lacks off-target reactivity is based solely on negative results against computationally predicted candidates. This does not rule out cross-reactivity with peptides not captured by the prediction algorithm. The fatal cardiac toxicity in the MAGE-A3 TCR-T trial was caused by a Titin-derived peptide that was not predicted by standard methods, highlighting the inadequacy of computational-only approaches.\n\"we recommend the use of a combinatorial peptide library scan followed by screening against additional cell subsets to validate TCR specificity and detect off-target toxicity due to cross-reactivity directed against unrelated peptides before selecting candidate TCRs for clinical testing\" from [Bijen et al., 2018](https://pmc.ncbi.nlm.nih.gov/articles/PMC5993934/)\nPeer-reviewed literature explicitly recommends combinatorial peptide library (CPL) scanning as a prerequisite for TCR validation before clinical translation. CPL scans systematically test T cell recognition across a comprehensive peptide space, enabling detection of unexpected cross-reactive peptides that in silico methods miss. The reviewed paper does not employ this established methodology despite preparing the TCR for clinical use in the INVENT4GB trial.\n\"The results of the alanine scanning approach suggested a low risk for broad cross-reactivity of the 7B5 T cell clone... However, when we used the 9-mer CPL scan data to conduct a CPL-driven search of the human self-protein database, we found cross-reactivity directed against a peptide derived from the gene CDH13. This was confirmed by the ability of the 7B5 T cell clone\" from [Bijen et al., 2018](https://pmc.ncbi.nlm.nih.gov/articles/PMC5993934/)\nThis demonstrates a concrete example where alanine scanning (and by extension, in silico approaches) failed to predict off-target reactivity that was only detected through CPL scanning. The current paper's methodology closely mirrors the approach that missed CDH13 cross-reactivity in the cited study, suggesting a similar gap may exist in the PTPRZ1-TCR safety profile.\n\"A clinically relevant example of the dangers of this approach was recently reported in which unexpected cross-reactivity of an enhanced affinity TCR targeting HLA-A*01-restricted epitope from MAGE-A3 (A1-MAGE-A3) resulted in cardiovascular toxicity through recognition of an unrelated HLA-A*01 peptide, A1-Titin\" from [Cameron et al., 2016](https://www.nature.com/articles/srep18851)\nThe MAGE-A3 clinical trial resulted in fatal cardiac toxicity due to TCR cross-reactivity with Titin that was not predicted by preclinical safety assessments. This historical case underscores the critical importance of comprehensive empirical cross-reactivity screening beyond computational prediction, a gap that remains in the current study's methodology.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|76|Claude|2", "source": "prb", "split": "test", "paper_id": "prb76", "comment": "The paper's safety rationale for the PTPRZ1-TCR relies on the assertion that PTPRZ1 is barely expressed in adult tissues, but this contradicts multiple published studies demonstrating that PTPRZ1 is one of the most abundantly expressed genes in normal brain astrocytes and is expressed in neurons, oligodendrocytes, and oligodendrocyte precursor cells, raising concerns about potential on-target off-tumor neurotoxicity.\n\n\"PTPRZ1 is, if at all, barely expressed across adult tissues, and the TCR was isolated from a vaccinated patient without notable adverse events; hence, we hypothesized that the TCR had undergone thymic selection, making both off-target and on-target off-tumor toxicities unlikely.\"\nThis statement forms a key safety argument for proceeding to clinical trials. However, the claim that PTPRZ1 is \"barely expressed\" in adult tissues is not consistent with the extensive body of literature documenting significant PTPRZ1 expression in normal adult brain cells, particularly astrocytes. The absence of adverse events in the vaccinated patient may reflect the limited systemic exposure from peptide vaccination versus adoptive cell transfer.\n\"Ptprz1 is one of the most abundantly expressed genes in cortical astrocytes during development and is strongly enriched in astrocytes compared to all other brain cell types; however, its function in astrocytes is unknown. Ptprz1 encodes for protein tyrosine phosphatase receptor type Z1 (PTPRZ1)\" from [Spitzer et al., 2023](https://pmc.ncbi.nlm.nih.gov/articles/PMC12248130/)\nThis recent publication directly contradicts the paper's claim by demonstrating that PTPRZ1 is among \"the most abundantly expressed genes\" in astrocytes. The paper also notes that \"expression remains high throughout the lifespan,\" indicating persistent adult expression. This raises significant concerns about potential on-target off-tumor toxicity to normal astrocytes when TCR-T cells are delivered intracerebroventricularly.\n\"PTPRZ is highly expressed in glial cells of the central nervous system (CNS), including oligodendrocyte precursor cells (OPCs), astrocytes, and oligodendrocytes\" from [Fujikawa et al., 2022](https://pmc.ncbi.nlm.nih.gov/articles/PMC9024684/)\nThis review article documents high PTPRZ expression across multiple normal CNS cell types including astrocytes, OPCs, and oligodendrocytes. Given that the authors propose intracerebroventricular delivery of TCR-T cells, the potential for these cells to encounter and react against PTPRZ1-expressing normal brain cells requires thorough experimental assessment that is absent from the current study.\n\"Distinct expression in brain, both in subsets of neurons and a subset of glial cells\" from [Human Protein Atlas](https://www.proteinatlas.org/ENSG00000106278-PTPRZ1)\nThe Human Protein Atlas, a comprehensive resource for human protein expression, documents PTPRZ1 expression in both neurons and glial cells of normal brain tissue. This contradicts the paper's assertion of minimal adult tissue expression and highlights a potential safety concern that is not adequately addressed in the preclinical assessment.\n\"found PTPRZ1 to be highly expressed in malignant cells but not in immune cells such as T cells and macrophages, nor in normal glial cells, oligodendrocytes and microglia (Fig. 1B and Fig. S1D-H).\"\nThe paper's own scRNA-seq analysis claims PTPRZ1 is not expressed in \"normal glial cells, oligodendrocytes and microglia.\" This appears to conflict with the external literature cited above, suggesting potential issues with the analysis or interpretation of scRNA-seq data, or differences in what constitutes \"normal\" glial cells in the tumor-adjacent microenvironment versus truly healthy brain tissue.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|76|Claude|3", "source": "prb", "split": "test", "paper_id": "prb76", "comment": "The in vivo efficacy and safety studies rely on U87 glioblastoma cells engineered to express a tandem minigene (TMG) rather than endogenous PTPRZ1, implanted in immunodeficient mice that lack human normal tissue expression of PTPRZ1, thereby preventing assessment of on-target off-tumor toxicity and limiting the translational relevance of efficacy findings.\n\n\"Since the complete open reading frame (ORF) of PTPRZ1 is large (~7kbp), we generated a well-characterized HLA-A*02+ GB cell line (U87) stably expressing a tandem minigene (TMG) encoding several antigens derived from the GAPVAC-101 and IMA950 trials, including the PTPRZ1 antigens of interest.\"\nThe in vivo model relies on artificial overexpression of the target epitope via TMG rather than testing against endogenous PTPRZ1 expression. This approach cannot assess whether TCR-T cells can effectively recognize the naturally processed and presented PTPRZ1 epitope at physiological expression levels in vivo, which is crucial for predicting clinical efficacy.\n\"Of note, in our glioma model overexpressing but not depending on TMG in vivo, we found loss of the cognate antigen (Fig. 4L). It remains speculative, if this is a unique feature of our model as PTPRZ1 expression remained stable during disease progression in patients.\"\nThe authors acknowledge that their model shows antigen loss, casting doubt on whether the model accurately recapitulates human GB biology. The TMG-based system creates an artificial selection pressure that may not reflect the biology of endogenous PTPRZ1-expressing tumors, limiting the interpretability of efficacy results.\n\"In contrast to human GBM, U87 tumors implanted into mice are well demarcated and surrounded by reactive astrocytes without diffuse infiltration. The lack of tumor infiltration is a significant limitation of the U87 line as diffuse infiltration is a key feature of human GBM\" from [Haddad et al., 2021](https://pmc.ncbi.nlm.nih.gov/articles/PMC8403483/)\nThe U87 model has well-documented limitations for studying GBM, lacking the infiltrative growth pattern characteristic of human glioblastoma. This limitation is particularly relevant for TCR-T cell therapy studies where the ability of effector cells to reach invasive tumor cells at the tumor margins is critical for therapeutic success.\n\"The model lacks key features of clinical glioblastoma, including invasive growth and microenvironmental complexity, and concerns have been raised regarding genetic drift and divergence from the original tumor phenotype\" from [Altogen Labs](https://altogenlabs.com/xenograft-models/brain-cancer-xenograft/u87-xenograft-model/)\nMultiple sources document that U87 xenografts diverge significantly from clinical GBM characteristics. Importantly, immunodeficient mouse hosts lack the human immune cells and PTPRZ1-expressing normal tissues that would be present in patients, making it impossible to assess potential on-target off-tumor neurotoxicity before clinical translation.\n\"Traditional in vivo model systems are either human xenografts in immunodeficient mice or syngeneic tumors grown in immunocompetent mice. Both approaches miss key elements of the tumor microenvironment, potentially contributing to the mismatch between pre-clinical and clinical results in immunotherapy\" from [Taconic NOG-EXL humanization study](https://www.taconic.com/content/dam/taconic/assets/print-assets/posters/Severely_immunodeficient_NOG-EXL_mice_allow_for_humanization_and_development_of_a_human_glioblastoma-derived_tumor_microenvironment.pdf)\nThis highlights the recognized limitation that xenograft models in immunodeficient mice cannot recapitulate the complex tumor-immune interactions relevant to immunotherapy efficacy and safety. For TCR-T cell therapy specifically, the inability to model interactions with host immune cells and normal tissues expressing the target antigen represents a significant gap in preclinical validation.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|76|Claude|4", "source": "prb", "split": "test", "paper_id": "prb76", "comment": "The study demonstrates that intravenous (i.v.) delivery of PTPRZ1-TCR-T cells alone was not efficacious against intracranial tumors, and therapeutic benefit only occurred with combined i.v. and intracerebroventricular (i.cv.) delivery, which represents a significantly more invasive clinical approach with added procedural risks that may limit patient eligibility and clinical implementation.\n\n\"Intravenous adoptive cell transfer against experimental brain tumors alone was not efficacious, but the addition of intracerebroventricular administration of PTPRZ1-TCR-T resulted in potent tumor rejection.\"\nThe abstract explicitly states that i.v. delivery alone failed to control intracranial tumors. This is a significant limitation because i.v. delivery is the standard, minimally invasive route for adoptive cell therapy. The requirement for i.cv. delivery necessitates surgical implantation of an Ommaya reservoir, limiting the therapy to patients who can tolerate this procedure.\n\"A recent study has demonstrated that repeated systemic i.v. CAR-T delivery does not result in glioblastoma control in a phase I trial, not even in a combinatorial treatment with immune checkpoint blockade.\"\nThe authors acknowledge that i.v. delivery has already failed in clinical CAR-T trials for GBM, supporting their rationale for i.cv. delivery. However, this also highlights that the requirement for intracranial delivery is a known challenge in the field that this study does not overcome; rather, it accepts this limitation and builds upon it.\n\"when we delivered PTPRZ1-TCR-T into mice bearing intracranial U87 TMG tumors i.v. (Supplementary Fig. 8a), no survival benefit was observed.\"\nSupplementary data confirms complete lack of efficacy with i.v. delivery in the intracranial model. While the combined i.v. + i.cv. approach showed efficacy, the clinical burden of requiring intracerebroventricular delivery substantially narrows the patient population eligible for this therapy and increases procedural complexity and risk.\n\"Although i.v. delivery of TCR-T cells in our experimental glioblastoma model was not efficacious, with our current knowledge, we cannot exclude its potential efficacy in glioblastoma patients.\"\nThe authors speculate that i.v. delivery might still work in humans despite clear negative results in their preclinical model. This acknowledgment, while appropriately cautious, highlights uncertainty about whether i.v. administration could provide any therapeutic benefit in the planned clinical trial, making the complex i.cv. delivery potentially essential for any clinical activity.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|76|GPT|1", "source": "prb", "split": "test", "paper_id": "prb76", "comment": "This paper makes an overconfident safety conclusion (Validity, Conclusions) that the PTPRZ1^{1814-1822} TCR lacks clinically relevant off-target reactivity, based on the limited off-target evaluation described for the ARDitox+Jurkat reporter assays.\n\n\"The validated vaccine-induced TCR recognized the endogenously processed antigen without cross-reactivity to *in silico* predicted low-risk off-targets.\" \nThis sentence is framed as a broad safety-relevant conclusion, but the qualifier \"*in silico* predicted\" materially narrows what has been tested. In engineered TCR therapies, clinically relevant cross-recognition can occur outside whatever candidate list a computational pipeline produces, so absence of reactivity to a short, pre-selected peptide panel does not establish overall safety. The statement also does not clarify what classes of risk remain untested (e.g., rare-peptide cross-reactivity, post-translationally modified ligands, or unexpected motifs). Because the paper is explicitly motivating a first-in-human trial, the evidentiary standard for safety claims is higher than for a purely mechanistic study. As written, the sentence can be interpreted as evidence of general non-cross-reactivity rather than \"no signal in this particular limited assay.\" This overreach affects how readers interpret the readiness of the construct for clinical translation.\n\"No high-risk (safety score < 3) potential off-targets were predicted while 12 low-risk (safety score > 3) off-targets with relevant presentation probabilities on HLA-A*02 were predicted. In a subsequent Jurkat reporter assay, we did not find reactivity against any of these 12 potential off-targets (Fig. 2F).\" \nThe paper's experimental off-target testing is restricted to 12 peptides chosen by ARDitox, and the readout is a Jurkat reporter assay, which is not equivalent to primary T-cell cytotoxicity or activation in relevant tissue contexts. This design is vulnerable to false negatives if the true cross-reactive ligand is not among the predicted candidates or if the assay context does not recapitulate antigen processing/presentation and co-stimulation. The manuscript does not present complementary screening approaches commonly used in the field to broaden coverage (e.g., scanning libraries or systematic motif searches coupled to functional testing), so the negative result is not strongly informative about real-world risk. The authors' own narrative frames this as an assessment of the \"safety profile\" rather than a narrow computationally guided check, which increases the chance of misinterpretation. Because the proposed clinical route includes CNS delivery, even low-frequency cross-reactivity could have high-consequence outcomes. Therefore, the evidence provided does not justify the strength of the safety language.\n\"Off-targets were predicted as described previously46. Briefly, 9-mer peptides of human proteome that share at least 5 amino acids with the target epitope were shortlisted.\" \nThis method description shows that the candidate universe is constrained by a sequence-similarity heuristic (≥5 shared residues), which can systematically exclude unexpected cross-reactive peptides. In practice, TCR recognition can tolerate non-intuitive substitutions and still cross-recognize peptides that do not meet a simple shared-residue threshold, especially when only a subset of peptide positions dominates recognition. The paper does not provide evidence that the chosen heuristic is sufficiently sensitive for this TCR, nor does it quantify how many plausible candidates remain untested after filtering. Limiting candidates in this way can make downstream \\\"no reactivity\\\" results difficult to interpret as a global safety statement. The lack of orthogonal discovery methods (e.g., unbiased peptide library screens) means the negative Jurkat results could reflect incomplete search rather than true specificity. This is a major validity concern for any claim of clinical-grade safety.\n\"Extensive preclinical investigations revealed no off-target antigen recognition concerns; nonetheless, administration to patients of T cells expressing the affinity-enhanced MAGE A3 TCR resulted in a serious adverse event (SAE) and fatal toxicity against cardiac tissue.\" [[1]](#ref1)\nThis external example directly demonstrates that seemingly thorough preclinical specificity testing can still miss clinically catastrophic cross-reactivity in engineered TCR settings. The key methodological lesson is that negative results from limited panels of normal cells or predicted peptides do not guarantee absence of off-target toxicity in vivo. The paper under review uses a narrower approach (AI-predicted peptide panel + Jurkat reporter), so it is at least as vulnerable to the same class of failure. The citation therefore undermines the manuscript's implicit inference that lack of reactivity to predicted candidates establishes safety. This comparison is particularly relevant because both contexts involve TCR-engineered T cells and the central risk is unexpected peptide cross-recognition. Consequently, the manuscript's safety conclusion is not robust when judged against documented failures in the literature.\n\"Strategies such as peptide scanning and the use of more complex cell cultures are recommended in preclinical studies to mitigate the risk of off-target toxicity in future clinical investigations.\" [[1]](#ref1)\nThis recommendation highlights the gap between best-practice safety screening and what is reported in the manuscript. The reviewed paper does not present peptide-scanning style breadth (it tests only 12 predicted peptides) and relies heavily on a Jurkat reporter system rather than more biologically complex models of antigen presentation. When a study is positioned as enabling a \\\"first-in-human\\\" trial, following (or at least explicitly justifying deviations from) recommended mitigation strategies becomes crucial for credibility. The quote also clarifies that expanding screening is not a cosmetic improvement but a response to known, high-stakes safety failures. Because the manuscript does not implement these approaches, its safety claims should be tempered or supported with additional experiments. The absence of such breadth is therefore a major issue affecting validity and translational interpretation.\n\nReferences:\n[1] [Cameron BJ et al. Identification of a Titin-Derived HLA-A1-Presented Peptide as a Cross-Reactive Target for Engineered MAGE A3-Directed T Cells. *Science Translational Medicine* (2013).](https://pmc.ncbi.nlm.nih.gov/articles/PMC6002776/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|76|GPT|2", "source": "prb", "split": "test", "paper_id": "prb76", "comment": "This paper makes a likely incorrect or overstated target-selectivity claim (Validity, Conclusions) that PTPRZ1 is \"exclusively\" malignant and \"barely\" expressed in adult tissues, in the antigen-expression and safety-justification sections used to argue low on-target/off-tumor risk.\n\n\"Single-cell sequencing of primary brain tumor samples showed *PTPRZ1* overexpression exclusively in malignant cells and most pronounced in GB stem cells and astrocyte (AC)- or oligodendrocyte-progenitor (OPC)-like cells.\"\nThis sentence asserts exclusivity (a strong claim) rather than reporting relative enrichment in malignant compartments, and it is used to motivate clinical targeting. In glioblastoma, target selection is safety-critical because normal brain expression can translate into on-target neurologic toxicity, especially with locoregional delivery. An exclusivity claim requires careful comparison not only to immune/stromal cells in tumors but also to appropriate normal CNS reference cell types and states. The manuscript's later rationale for low off-tumor toxicity depends on this exclusivity interpretation, so any overstatement materially changes the risk assessment. Importantly, the statement is not phrased as dataset-conditional (e.g., \\\"in the analyzed datasets\\\"), which makes it easier to misread as a general biological fact. Because PTPRZ1 biology is tightly linked to CNS development and glial lineage, the burden of proof for exclusivity is high.\n\"In order to detail *PTPRZ1* at cellular resolution, we interrogated publicly available GB and isocitrate dehydrogenase (IDH)-mutant glioma single-cell RNA-seq (scRNA-seq) datasets40,41, and found *PTPRZ1* to be highly expressed in malignant cells but not in immune cells such as T cells and macrophages, nor in normal glial cells, oligodendrocytes and microglia (Fig. 1B and Fig. S1D-H).\"\nThis claim is central to the manuscript's target selectivity argument, because it explicitly denies expression in \"normal glial cells\" and oligodendrocytes. However, glioblastoma arises in a CNS environment where many glial programs are shared between malignant and non-malignant lineages, and scRNA-seq annotations and detection thresholds can easily obscure low-to-moderate expression in specific glial subsets. The statement is also difficult to reconcile with the broader neurobiology of the PTPRZ/PTPRZ1 family, which is commonly described as CNS/glia-associated, suggesting that the manuscript may be overinterpreting tumor-only specificity from limited comparisons. If normal glial expression exists (even in subsets), then on-target off-tumor risk is not negligible, especially for intracerebroventricular administration. Because the paper uses this as evidence of a favorable safety profile, any mischaracterization undermines validity. The issue is not minor: it directly affects whether PTPRZ1 is an appropriate therapeutic target.\n\"*PTPRZ1* is, if at all, barely expressed across adult tissues^{24}, and the TCR was isolated from a vaccinated patient without notable adverse events^{23}; hence, we hypothesized that the TCR had undergone thymic selection, making both off-target and on-target off-tumor toxicities unlikely.\"\nThis is an explicit safety inference: low adult expression is used to argue low on-target/off-tumor toxicity, and thymic selection is invoked to downplay off-target risk. Even if thymic selection occurred, it does not guarantee absence of clinically meaningful cross-reactivity or safe targeting of low-level self-expression in essential tissues. The claim of \"barely expressed\" is particularly consequential in the CNS, where modest expression in neurons or glia could still be dangerous under high-avidity TCR-T exposure. The manuscript does not provide a comprehensive adult-brain expression assessment tied to the specific peptide-HLA presentation context, which would be needed to support this inference. Because this reasoning is used to justify moving toward a first-in-human trial, it should be backed by stronger tissue-level evidence than is shown. Without that, the safety argument is not reliable.\n\"PTPRZ1 is involved in central nervous system development\\(^{25,26}\\).\"\nEven within the manuscript, PTPRZ1 is framed as a CNS-involved molecule, which raises a priori concern about normal CNS expression and function. While developmental involvement does not automatically imply high adult expression, it is inconsistent with treating CNS expression as negligible without careful qualification. Given that the therapeutic strategy includes intraventricular delivery (directly exposing CNS compartments), the default expectation should be to proactively rule out glial/neuronal expression rather than assume it away. The manuscript does not bridge this logical gap: it cites developmental roles but then asserts minimal adult expression to argue safety. This internal tension suggests that the selectivity and safety narrative may be incomplete. It matters because the risk profile in brain-targeted cell therapy hinges on normal CNS expression patterns.\n\"PTPRZ is highly expressed in glial cells of the central nervous system (CNS), including oligodendrocyte precursor cells (OPCs), astrocytes, and oligodendrocytes\" [[2]](#ref2)\nThis review statement directly contradicts the manuscript's claim that PTPRZ1 is not expressed in \"normal glial cells\" and oligodendrocytes. Although the review discusses PTPRZ (the receptor type Z family; closely aligned with the PTPRZ1 nomenclature used in the manuscript), the key point is that the target is not generally regarded as tumor-exclusive in the CNS. If the target is normally expressed in OPCs/astrocytes/oligodendrocytes, then both on-target off-tumor toxicity and interpretation of scRNA-seq \\\"specificity\\\" require more caution. The contradiction is substantial because it impacts whether the antigen is a safe immunotherapy target and whether the manuscript's selectivity conclusions are robust. It also implies that dataset-dependent absence in some scRNA-seq analyses should not be generalized to biology-wide absence. Therefore, the manuscript's tumor-exclusivity framing is not supported when compared to established CNS expression descriptions.\n\"Protein tyrosine phosphatase receptor type Z (PTPRZ) is a membrane protein that is abundantly expressed in CNS glial cells ([4](#bib4)), including oligodendrocyte precursor cells, astrocytes, and oligodendrocytes ([5](#bib5)).\" [[3]](#ref3)\nThis primary-research paper again emphasizes abundant expression in CNS glial cells, reinforcing that CNS/glial expression is a well-supported feature rather than an edge-case claim. The reviewed manuscript uses \"barely expressed across adult tissues\" to argue away on-target off-tumor toxicity, but CNS is an adult tissue, and this quote indicates substantial glial expression in that compartment. Even if transcript levels differ between malignant and normal cells, abundant normal glial expression undercuts any statement of exclusivity and demands additional safety testing (e.g., primary human glial cultures, brain organoid co-cultures, or peptide presentation assays). The contradiction is critical because it could mean the therapy targets non-malignant CNS cells, which would be prohibitive for publication-grade validity if unaddressed. It also suggests the manuscript's scRNA-seq-based \\\"not in normal glia\\\" conclusion may reflect dataset limitations rather than true absence. Thus, the paper's target-selectivity and safety conclusions are not robust.\n\"Consensus (human tissue): | Tissue enriched (Brain) Detected in many\" [[4]](#ref4)\nIndependent atlas-style resources classify PTPRZ1 as brain-enriched, which directly challenges the manuscript's implication that adult-tissue expression is negligible in a clinically reassuring way. A target enriched in brain warrants heightened caution for any therapy delivered to, or trafficking through, CNS compartments. The paper's safety argument relies on low expression in adult tissues, but a \"Brain\" enrichment calls for much more granular evidence (which brain cell types, what levels, and whether the specific peptide is presented on HLA-A*02). The quote does not by itself prove peptide presentation; however, it demonstrates that the manuscript's broad tissue-expression premise is not aligned with widely used reference datasets. When a key premise is contested by external resources, conclusions built on it should be weakened or experimentally revalidated. Therefore, the manuscript's selectivity framing is questionable and affects validity.\n\nReferences:\n[2] [Nagai K, Fujii M, Kitazume S. Protein Tyrosine Phosphatase Receptor Type Z in Central Nervous System Disease. *International Journal of Molecular Sciences* (2022).](https://pmc.ncbi.nlm.nih.gov/articles/PMC9024684/)\n[3] [Nagai K et al. Brain-specific glycosylation enzyme GnT-IX maintains levels of protein tyrosine phosphatase receptor PTPRZ, thereby mediating glioma growth. *Journal of Biological Chemistry* (2023).](https://pmc.ncbi.nlm.nih.gov/articles/PMC10480537/)\n[4] [The Human Protein Atlas. Expression of PTPRZ1 in cancer - Summary.](https://www.proteinatlas.org/ENSG00000106278-PTPRZ1/cancer)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|76|GPT|3", "source": "prb", "split": "test", "paper_id": "prb76", "comment": "This paper draws conclusions about potent therapeutic efficacy and off-the-shelf readiness (Conclusions, Validity, Data and methodology) from in vivo experiments that rely on an engineered tandem-minigene (TMG) antigen system in U87 tumors and on intracerebroventricular delivery after intravenous delivery fails, limiting how strongly the results support efficacy against endogenous PTPRZ1 presentation in glioblastoma.\n\n\"Intravenous adoptive cell transfer against experimental brain tumors alone was not efficacious, but the addition of intracerebroventricular administration of PTPRZ1-TCR-T resulted in potent tumor rejection.\" \nThe abstract centers a strong efficacy narrative while simultaneously acknowledging that the clinically simpler systemic route (i.v.) did not work in their brain tumor model. Because trafficking, distribution, and antigen encounter dynamics differ substantially between i.v. and i.c.v. routes, efficacy under i.c.v. does not necessarily support an \"off-the-shelf\" paradigm unless the intended clinical administration is likewise locoregional and clearly justified. The statement \"potent tumor rejection\" also risks overgeneralization if it is driven by a specific engineered model that may not match endogenous antigen processing and density. For validity, the key question is whether the observed rejection reflects recognition of naturally processed PTPRZ1 peptide in realistic GB contexts, or whether it reflects properties of the model and delivery. The manuscript later shows antigen-loss behavior in the model, which further complicates interpretation of durable control. Thus, the headline conclusion is stronger than the underlying evidence supports for general GB therapy.\n\"Since the complete open reading frame (ORF) of *PTPRZ1* is large (~7kbp), we generated a well-characterized HLA-A*02+ GB cell line (U87) stably expressing a tandem minigene (TMG) encoding several antigens derived from the GAPVAC-101 and IMA950 trials, including the PTPRZ1 antigens of interest (Fig. S4A,B and Table. S1)^{23,45}.\"\nThis sentence establishes that key validation steps (including in vivo brain tumor work later in the manuscript) are anchored to a surrogate antigen-expression system rather than endogenous PTPRZ1 processing. A tandem minigene can change epitope generation and abundance compared to the native full-length protein (e.g., altered flanking sequences and processing), which can inflate apparent TCR performance. The paper does present ligandomics and primary-cell-line killing, but the most prominent in vivo intracranial efficacy is in U87 TMG tumors, which is an engineered context. That makes it hard to attribute tumor control to recognition of naturally presented PTPRZ1^{1814-1822} in vivo at physiologic antigen densities. For conclusions about clinical efficacy, the gold standard is demonstrating activity in models where the antigen is endogenously expressed and presented, not introduced via a minigene. Therefore, the model choice limits how strongly the in vivo results support the translational claims.\n\"Indeed, when we delivered PTPRZ1-TCR-T into mice bearing intracranial U87 TMG tumors i.v. (Fig. S8A), no therapeutic effect was observed (Fig. S8B). Hence, we adapted our ACT regime to two doses of intracerebroventricular (i.cv.) ACT following one dose of i.v. ACT (Fig. 4C).\"\nThis explicitly shows that the therapy's efficacy in the intracranial setting is contingent on changing the route to i.c.v., which is a major experimental intervention that changes exposure and biodistribution. While locoregional delivery can be clinically relevant in neuro-oncology, the manuscript should then align its claims and framing around that route rather than implying broad off-the-shelf applicability from systemic delivery. The lack of i.v. efficacy also implies that any clinical success would depend on neurosurgical access and local delivery logistics, which are nontrivial and should be treated as core constraints rather than as a minor optimization. Moreover, because the intracranial model is U87 TMG, the conclusion is doubly contingent (engineered antigen + specialized delivery). This combination makes it difficult to generalize to heterogeneous, patient-derived GB with endogenous PTPRZ1 peptide presentation. As a result, the strength of the in vivo efficacy conclusion is not well supported.\n\"We thereby examined antigen expression with RNAscope™ and found that TMG transcripts were greatly diminished in the recurrent tumors (Fig. 4L,M). These data demonstrate the on-target activity of PTPRZ1-TCR-T and highlights the ACT route-dependent efficacy in experimental GB. Intriguingly, the reactive TCR-T cell product persists in experimental brain tumors, and the relapse is driven by downregulation and/or loss of the tandem antigens in this model.\"\nThis passage concedes that relapse in the key intracranial model is linked to loss/downregulation of the engineered TMG antigens, which is a model-specific escape mechanism. That undermines the generality of the efficacy claim, because antigen dynamics for an artificial minigene cassette may differ from endogenous PTPRZ1 regulation in patient tumors. It also complicates interpretation of the study's headline \\\"potent tumor rejection\\\" because the model's durability is limited by loss of the engineered antigen rather than by clinically realistic immune escape pathways. The authors argue that this is not necessarily expected clinically, but that remains speculative without in vivo data in endogenous-expression models. In effect, the manuscript demonstrates that the therapy can apply strong selection pressure on an engineered target, but not that it will control naturally expressing GB over time. This is a significant limitation for both validity and the reliability of the conclusions.\n\"i.c. 150k U87 TMG inoculation\" and \"p = 0.3294\" (survival after i.v. dosing in the i.c. model)\nThe supplementary figure text confirms the engineered nature of the intracranial model (U87 TMG) and reports a non-significant survival result under the i.v.-only condition (p=0.3294). This supports the manuscript's own statement that systemic delivery was not efficacious, and it shows that the positive brain-tumor efficacy narrative depends on subsequent i.c.v. administration. Because the model is engineered and i.v. fails, the results do not strongly justify broad claims of efficacy for an off-the-shelf product unless the intended human administration is similarly locoregional and the model more closely matches endogenous antigen biology. The p-value also illustrates that, at least in this configuration, the effect is not robust to route changes, which is an important constraint for translation. Reporting these details only in supplementary text (without integrating their implications into the main claims) risks overstating general efficacy. Thus, this evidence supports the criticism that the conclusions are stronger than warranted.\n\"We find that the DNA profile of the widely used glioma cell line U87MG is different from that of the original cells and that it is likely to be a bona fide human glioblastoma cell line of unknown origin.\" [[5]](#ref5)\nThis literature statement highlights a well-known translational limitation of U87-based models: even if U87 behaves as a glioblastoma-like line, its provenance and representativeness are uncertain. The reviewed manuscript anchors major parts of its in vivo intracranial efficacy story on intracranial U87 TMG tumors, so any shortcomings of U87 as a GB surrogate directly affect how strongly efficacy generalizes to patient tumors. This does not invalidate the study outright, but it raises the bar for additional validation in more representative systems (e.g., patient-derived xenografts with endogenous antigen expression/presentation). When a model is both of uncertain origin and engineered to express a tandem minigene, external generalization becomes even weaker. The quote therefore supports that the in vivo efficacy evidence, while interesting, is insufficiently definitive for the breadth of translational conclusions drawn. This is a major conclusions/validity issue rather than a cosmetic model-choice preference.\n\nReferences:\n[5] [Allen M et al. Origin of the U87MG glioma cell line: Good news and bad news. *Science Translational Medicine* (2016).](https://www.science.org/doi/10.1126/scitranslmed.aaf6853)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|76|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb76", "comment": "The study fails to assess on-target/off-tumor toxicity in normal brain tissue, which is a critical safety concern given the expression of PTPRZ1 in the adult human brain. The experimental design explicitly prevents such assessment by using B2M-deficient organoids and non-HLA-transgenic mice.\n\n\"PTPRZ1 is, if at all, barely expressed across adult tissues\"\nThis claim contradicts established expression data. The Human Protein Atlas indicates that PTPRZ1 is \"Tissue enriched (Brain)\" [1], suggesting significant expression in normal adult brain tissue. This raises a major concern for on-target/off-tumor toxicity, potentially leading to severe adverse events like encephalitis, which the authors dismiss without sufficient evidence.\n\"host feeder organoid cells are engineered to be EGFP-expressing and B2M-deficient\"\nBy using B2M-deficient host cells in the IPTO model, the authors engineered the normal brain cells to lack MHC Class I expression. This prevents the TCR-T cells from recognizing and killing normal cells even if they express the antigen, thereby masking any potential on-target/off-tumor toxicity in this model.\n\"NOD.Cg-Prkdcscid H2-K1lmtBpe H2-Ab1lem1Mvw H2-D1lmtBpe Il2rgtm1Wjl/SzJ (NSG MHC KO) mice were bred at the DKFZ animal facility.\"\nThe in vivo experiments utilized MHC knockout mice that do not express human HLA-A*02. Consequently, the human TCR-T cells could not recognize endogenous mouse PTPRZ1 (assuming cross-reactivity or conservation) on normal tissues, rendering the in vivo model incapable of assessing on-target/off-tumor toxicity.\n\nReferences:\n[1] The Human Protein Atlas. PTPRZ1. https://www.proteinatlas.org/ENSG00000106278-PTPRZ1/tissue", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|76|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb76", "comment": "The demonstration of in vivo efficacy relies exclusively on a glioblastoma cell line (U87) engineered to overexpress the antigen via a Tandem Minigene (TMG), which does not reflect physiological antigen levels and likely overestimates therapeutic efficacy.\n\n\"we generated a well-characterized HLA-A*02+ GB cell line (U87) stably expressing a tandem minigene (TMG)...\"\nThe use of a cell line engineered to express the antigen from a strong promoter (TMG) creates an artificial system with potentially supraphysiological antigen density. This does not accurately model the heterogeneous and often lower expression levels of endogenous PTPRZ1 found in patient tumors.\n\"When we delivered PTPRZ1-TCR-T into mice bearing intracranial U87 TMG tumors...\"\nThe authors demonstrated in vitro cytotoxicity against primary cell lines with endogenous PTPRZ1 expression (e.g., P3), but chose not to use these more relevant models for the critical in vivo efficacy studies. Relying solely on the TMG overexpression model for in vivo validation weakens the translational relevance of the findings.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|76|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb76", "comment": "The conclusion that tumor recurrence is driven by antigen loss is based on the downregulation of the artificial TMG construct, which is an artifact of the model rather than a representative biological mechanism of immune escape for the endogenous gene.\n\n\"TMG transcripts were greatly diminished in the recurrent tumors\"\nThe observed loss of TMG expression is likely due to plasmid instability, silencing of the exogenous promoter, or selection against cells maintaining the artificial construct, rather than a true biological downregulation of the endogenous PTPRZ1 gene.\n\"relapse is driven by downregulation and/or loss of the tandem antigens in this model\"\nDrawing conclusions about clinical resistance mechanisms (antigen loss) from the loss of an artificial minigene is misleading. In patients, PTPRZ1 is a genomic gene, and its downregulation would require different mechanisms (e.g., epigenetic silencing, mutation) that are not modeled by the loss of a TMG plasmid.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|76|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb76", "comment": "The off-target safety profile was assessed solely based on *in silico* prediction and testing of a small number of peptides, which is insufficient to rule out cross-reactivity against the human proteome.\n\n\"No high-risk... potential off-targets were predicted while 12 low-risk... were predicted... we did not find reactivity against any of these 12\"\nRelying exclusively on *in silico* prediction (ARDitox) and testing only 12 peptides is not a comprehensive safety assessment. Standard practices for TCR development involve more rigorous screening, such as testing against a large panel of HLA-matched healthy tissue cells or using combinatorial peptide libraries to define the TCR recognition motif and identify unpredicted cross-reactivities [2, 3].\n\"PTPRZ1 is, if at all, barely expressed across adult tissues\"\nThis assumption, used to justify the limited safety testing, is contradicted by expression databases [1]. The lack of experimental screening against healthy tissues (e.g., normal brain, heart, liver) leaves a significant gap in the safety profile of the proposed therapy.\n\nReferences:\n[1] The Human Protein Atlas. PTPRZ1. https://www.proteinatlas.org/ENSG00000106278-PTPRZ1/tissue", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|76|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb76", "comment": "The first part of the study was performed using the U87 TMG cell line. I understand the reason for choosing U87, considering they are a well-characterized HLA-A02 cell line. However, U87 MG are not completely representative of a glioblastoma, for example, they are methylated in MGMT promoter. Therefore, did the authors compare the STR profile with their U87 cells to those of U87MG from ATCC?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|76|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb76", "comment": "I need to better understand why the authors observed \"no therapeutic effect\" using an IV administration as a single therapeutic modality, but a preclinical response when combined with IV and ICV.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|76|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb76", "comment": "Based on the evidence that pleiotrophin (PTN) is secreted by TAM, it is crucial to consider the potential influence of the tumor microenvironment on the efficacy of this therapeutic strategy.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|76|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb76", "comment": "Did the authors consider a combination treatment? Chemotherapy or radiotherapy, even for modulating the tumor microenvironment?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|76|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb76", "comment": "It is not clear how much antigen needs to be presented to effect clinical responses (the U87-transduced with the tandem mini-gene is great, but obviously has high antigen presentation); the spheroid data is helpful but is limited by in vitro nature.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|76|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb76", "comment": "It is not clear if targeting stemness (GSC's) will be sufficient for clinical responses in GBM. However, these are all things that will become clearer in the clinical trial – my only suggestion is that they be discussed, I don’t think it’s necessary to address these experimentally in this paper.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|76|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb76", "comment": "Figures should be numbered/labeled.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|76|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb76", "comment": "Figure 3H is confusing with the red PTPRZ TCR and the red CD8 and the blue Flu TCR and CD4. Figure 3K has a lot of colors for unclear reasons – donor, pink, and biorender cells. This needs to be simplified and clarified with simple labels instead of drawings.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|76|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb76", "comment": "In Figure 4, why do the authors think that there is no anti-tumor response after the first TCR injection (between day 9 and day 16?) is it because the tumor are too small to measure in that time? How accurately I can < 20 mm2 be measured?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|77|Claude|1", "source": "prb", "split": "test", "paper_id": "prb77", "comment": "The paper proposes a complex mechanism involving sequential 8π electrocyclization followed by metal carbene formation, but provides no DFT computational studies to validate these mechanistic claims. This represents a significant gap in methodological rigor for a study that makes novel mechanistic proposals about cascade cyclization processes.\n\n\"we speculated that the metal-catalyzed 5-endo-annulization of pyridine-alkyne might form zwitterionic vinyl metal species that might resonate to become a reactive conjugated 8π electronic system and a metal carbene.\"\nThe paper uses hedging language (\"speculated,\" \"might\") when describing the key mechanistic pathway, indicating uncertainty about the proposed mechanism. For such a novel cascade mechanism involving simultaneous 8π electrocyclization and metal carbene formation, modern synthetic chemistry standards call for computational validation. The proposed mechanism involves several unprecedented intermediates that would benefit from DFT energy profile calculations to establish the feasibility and energetics of each step.\n\"Electrocyclization reactions can be driven by heating and are not affected by external conditions. However, the reactivity of metal carbene is closely related to the reaction system. Thus, electrocyclization might be conducted for constructing seven-membered ring structures\"\nThe paper makes assumptions about the timing and coupling of electrocyclization with metal carbene formation without computational evidence. The claim that electrocyclization occurs simultaneously with or prior to metal carbene involvement requires theoretical support, as the relative energies of these pathways would determine the actual reaction course. Without computational studies, alternative mechanisms cannot be rigorously excluded.\n\"Using DFT and the IBO approach, we evaluated the π-stabilizing effects of organic substituents at the carbene carbon atom in the gold carbene complex 8.\" from [Wang et al., Nature Communications (2017)][1]\nThis reference demonstrates that DFT calculations and intrinsic bond orbital (IBO) analysis are standard approaches for characterizing metal carbene intermediates in cyclization reactions. The Wang et al. study isolated gold and copper carbene intermediates and used computational analysis to understand their bonding properties. The current paper proposes similar copper carbene intermediates but lacks any computational characterization.\n\"A computational investigation towards substitution effects on 8π electrocyclisation of octatetraenes... Activation energies (ΔG‡, kcal mol−1) using M06-2X/6-31+G(d) for electrocyclic ring-closure of variously functionalised 2,Y-disubstituted octatetraenes\" from [RSC Advances (2023)][2]\nThis computational study demonstrates that DFT methods (M06-2X/6-31+G(d)) are routinely applied to understand 8π electrocyclization reactions, including predicting activation energies and stereochemical outcomes. The current paper's claim of 8π electrocyclization in a complex polycyclic system would be significantly strengthened by analogous computational analysis to validate the proposed pathway.\n\nReferences:\n[1] [Wang, J. et al. Synthesis and structures of gold and copper carbene intermediates in cyclization oxidation. Nature Communications 8, 14625 (2017).](https://www.nature.com/articles/ncomms14625)\n[2] [Saha, R. K. et al. A computational investigation towards substitution effects on 8π electrocyclisation of octatetraenes. RSC Advances 13, 28959 (2023).](https://pmc.ncbi.nlm.nih.gov/articles/PMC10587816/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|77|Claude|2", "source": "prb", "split": "test", "paper_id": "prb77", "comment": "The paper claims that the seven-membered ring is formed via 8π electrocyclization, which according to Woodward-Hoffmann rules proceeds with defined stereochemistry (conrotatory under thermal conditions). However, the paper fails to discuss the stereochemical outcome of this electrocyclization step or provide evidence for stereocontrol at this stage.\n\n\"The key characteristics included the formation of a seven-membered ring by the 8π electrocyclization of various alkenes and aromatic heterocycles as π-components\"\nThe abstract claims 8π electrocyclization as a key feature, but the paper does not discuss the stereochemical consequences of this pericyclic reaction. According to Woodward-Hoffmann rules, thermal 8π electrocyclization is conrotatory and should generate predictable stereochemistry at the newly formed stereocenters. The absence of any discussion of expected versus observed stereochemistry is a significant omission for a paper claiming pericyclic reaction involvement.\n\"The stereo-controlled late-stage modification of some complicated pharmaceuticals indicated the versatility of this protocol.\"\nThe phrase \"stereo-controlled\" in the abstract refers to the late-stage modification (nucleophilic substitution) products, not to the electrocyclization step itself. Examination of Table 3 and Figure 2 shows that diastereoselectivity is discussed only for products derived from C-C cleavage with nucleophilic reagents. The paper conflates stereocontrol at different steps, which is misleading regarding the electrocyclization stereochemistry.\n\"According to these rules, electrocyclic ring closure of conjugated octatetraenes with 8π system is a thermally induced conrotatory process, which involves spontaneous rotation of the terminal olefin bonds of a tetraene.\" from [RSC Advances computational study][2]\nThe literature clearly establishes that 8π electrocyclization under thermal conditions must proceed conrotatorily with predictable stereochemical outcomes. The current paper invokes this reaction class but provides no stereochemical analysis. For a complete mechanistic picture, the paper should address whether the products exhibit the stereochemistry expected from conrotatory ring closure.\n\"the electrocyclic ring-closure is disrotatory under photochemical conditions and conrotatory under thermal conditions\" from [Woodward-Hoffmann rules, Wikipedia][3]\nThe Woodward-Hoffmann rules are foundational to understanding electrocyclic reactions. The paper cites Woodward and Hoffmann (references 44-45 in the paper) but does not apply their stereochemical predictions to interpret or validate the proposed mechanism. This represents an incomplete application of the theoretical framework the authors themselves invoke.\n\nReferences:\n[2] [Saha, R. K. et al. A computational investigation towards substitution effects on 8π electrocyclisation of octatetraenes. RSC Advances 13, 28959 (2023).](https://pmc.ncbi.nlm.nih.gov/articles/PMC10587816/)\n[3] [Woodward–Hoffmann rules. Wikipedia.](https://en.wikipedia.org/wiki/Woodward%E2%80%93Hoffmann_rules)", "reviewer_type": "ai", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|77|Claude|3", "source": "prb", "split": "test", "paper_id": "prb77", "comment": "The paper claims to demonstrate \"late-stage modification of pharmaceuticals,\" but examination of Figure 2 reveals that pharmaceutical fragments are incorporated into substrates before the key transformation, rather than being modified directly at a late stage. This conflicts with the accepted definition of late-stage functionalization in the field.\n\n\"The late-stage modification of pharmaceuticals is of significant importance for the discovering new drugs or improving bioactivity (Fig. 2). To further demonstrate the potential of this strategy, we examined the application of the ring-opening nucleophilic substitution in the late-stage modification of biologically active small molecules.\"\nThe paper claims late-stage modification of pharmaceuticals including Gemfibrozil, Indomethacin, Estrone, Riluzole, and Candesartan cilexetil. However, examination of Figure 2 shows that these pharmaceutical fragments are conjugated to the substrates prior to the cyclization reaction. The pharmaceuticals serve as nucleophiles attacking a pre-formed NCPC intermediate, rather than being directly modified at a late synthetic stage.\n\"We define LSF as a desired chemical transformation on a complex molecule, without the necessity for a preinstalled functional group that exclusively serves the purpose to enable the transformation.\" from [Ritter group, Max Planck Institute][4]\nAccording to this widely accepted definition from a leading expert in late-stage functionalization, LSF should occur on complex molecules without requiring pre-installation of reactive handles. In the current paper, the pharmaceutical fragments are pre-functionalized (e.g., as carboxylates or other nucleophiles) before being coupled with the NCPC core. This represents derivatization or conjugation rather than true late-stage functionalization.\n\"LSF of a complex molecule can access at least one new, desired, functionalized molecule that would be substantially more cumbersome or time-consuming to access synthetically otherwise.\" from [Ritter group, Max Planck Institute][4]\nTrue late-stage functionalization enables direct modification of complex pharmaceuticals. In this paper, the complex pharmaceuticals are used as building blocks that are attached to a newly constructed core, rather than being modified directly. The pharmaceutical molecules shown (Gemfibrozil, etc.) retain their original structures and are simply linked to the NCPC scaffold, which does not meet the definition of modifying the pharmaceutical itself at a late stage.\n\"The term late-stage functionalization (LSF)...describe transformations on complex molecules. Such reactions include catalytic and non-catalytic reactions, C–H functionalizations, and functional-group manipulations\" from [Börgel & Ritter, Chem (2020)][5]\nThe field defines LSF as transformations performed on pre-existing complex molecules. In contrast, the paper synthesizes substrates 3 that already contain pharmaceutical fragments attached via an ester or other linkage, then performs the NCPC formation cascade. The pharmaceutical moiety is a spectator group during the key transformation, not the site of modification.\n\nReferences:\n[4] [Ritter, T. Late-Stage Functionalization. Max Planck Institute for Coal Research.](https://www.kofo.mpg.de/647198/late-stage-functionalization)\n[5] [Börgel, J. & Ritter, T. Late-Stage Functionalization. Chem 6, 1877–1887 (2020).](https://www.sciencedirect.com/science/article/pii/S2451929420303570)", "reviewer_type": "ai", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|77|Claude|4", "source": "prb", "split": "test", "paper_id": "prb77", "comment": "The mechanistic studies (deuterium labeling experiments) only address the hydrogen source for the C-H bond cleavage step and do not provide direct evidence for the proposed 8π electrocyclization. Alternative cyclization pathways cannot be excluded based on the experiments presented.\n\n\"To understand this mechanism and elucidate some specific processes of the reaction, several control experiments were conducted. First, the deuterated starting material 1a' was exposed to the standard conditions. The NMR spectra showed that the reaction generated product 2a rather than the deuterated product 2a' (Fig. 4 a), indicating that the intramolecular 1, 2-hydride shift triggered by metal carbene was not involved in the process.\"\nThe deuterium labeling experiment conclusively demonstrates that the hydrogen in the product does not originate from a 1,2-hydride shift, and the D2O experiment confirms water as the proton source. However, neither experiment addresses whether the seven-membered ring is actually formed via 8π electrocyclization versus other possible cyclization mechanisms (such as direct nucleophilic cyclization or alternative metal-mediated pathways). The key mechanistic claim of 8π electrocyclization remains unsupported by direct experimental evidence.\n\"The freshly prepared 1a (0.05 mmol, 1.0 equiv.), CuTc (10.0 mol%), dried toluene (1.0 mL) and D2O (0.2 mL) were added to a 5.0 mL round bottom flask at room temperature, the mixture was stirred at 90 °C for 0.5 h and then cooled to room temperature.\"\nThis control experiment from the supporting information demonstrates that water is the proton source, which helps explain the final protonation step. However, this experiment provides no information about the cyclization mechanism itself. Kinetic isotope effect studies, radical trapping experiments, or isolation of intermediates would be needed to validate the proposed 8π electrocyclization pathway.\n\"Electrocyclization reactions can be driven by heating and are not affected by external conditions.\"\nThe paper assumes that thermal electrocyclization occurs because the reaction requires heating. However, elevated temperature is also required for many other cyclization mechanisms (nucleophilic cyclizations, metal-catalyzed processes). The observation that heating is required does not discriminate between electrocyclization and alternative pathways. Without additional evidence such as stereochemical analysis, kinetic measurements, or computational support, the electrocyclization mechanism remains speculative.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|77|Claude|5", "source": "prb", "split": "test", "paper_id": "prb77", "comment": "The paper reports that α-C-H cleavage is optimally catalyzed by CuTc (copper thiophene-2-carboxylate) while α-C-C cleavage requires Ag3PO4, but provides no mechanistic rationale for why these ostensibly related metal carbene-mediated processes require fundamentally different catalysts.\n\n\"Among them, CuTc was used to produce the cyclization product with the highest yield (96%) (Table 1, entry 9).\"\nFor C-H cleavage (forming products 2), copper catalyst CuTc provides 96% yield, while silver salts give only trace amounts. This establishes a strong preference for copper in the first transformation type.\n\"After extensive screening, we found that the silver salts highly stimulated the α-C-C cleavage. Finally, using silver phosphate as the catalyst and TEBA as an additive in the presence of NaOAc, product 4a was formed with an 80% yield\"\nFor C-C cleavage (forming products 4), the optimal catalyst switches to Ag3PO4 with 80% yield, while CuTc gives only 11% yield. This dramatic reversal in catalyst preference is noted but not explained. If both pathways proceed through similar metal carbene intermediates as proposed, the different optimal catalysts suggest fundamentally different mechanistic requirements that the paper does not address.\n\"The success of this divergent synthesis process depended on subtle differences in the reactivity between the starting material and the metal catalyst because both metal carbene of different reactivity triggered different transformations.\"\nThe paper acknowledges that \"subtle differences\" in reactivity exist but does not elaborate on what these differences are or why copper favors C-H cleavage while silver favors C-C cleavage. This vague explanation does not provide the mechanistic insight expected in a paper proposing a new metal carbene-mediated cascade reaction. Understanding why specific metals promote specific transformations would be valuable for both mechanistic understanding and synthetic applications.\n\"Switching Au(I) to various silver salts, such as AgSbF6, AgOTf, and Ag3PO4, yielded only trace amounts of the product (Table 1, entries 3−5).\"\nIn the C-H cleavage reaction, silver salts including Ag3PO4 perform poorly. However, Ag3PO4 is optimal for C-C cleavage. This suggests that the two transformations may not share the same rate-determining step or involve similar transition states despite both being proposed to proceed through metal carbene intermediates. A mechanistic discussion addressing this divergence would strengthen the paper's claims.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|77|GPT|1", "source": "prb", "split": "test", "paper_id": "prb77", "comment": "This paper makes mechanistic claims about (i) “8π electrocyclization” forming the seven-membered ring and (ii) a “metal carbene” that triggers α-C–H/α-C–C bond cleavage, but the mechanistic evidence provided (deuterated-substrate and D2O experiments) is not sufficient to validate these specific intermediates and steps.\n\n\"The key characteristics included the formation of a seven-membered ring by the 8π electrocyclization of various alkenes and aromatic heterocycles as π-components, in which metal carbene species generated that further induced the cleavage of the α-C-H or -C-C bond.\" \nThis sentence asserts a specific pericyclic step (8π electrocyclization) and a specific intermediate class (metal carbene) as the causal drivers of the bond-cleavage outcomes. Those assertions are not merely descriptive; they are mechanistic commitments that exclude other plausible stepwise cyclization/rearrangement scenarios that can also produce medium rings and cationic reactivity under coinage-metal catalysis. Because the paper’s central conceptual contribution is framed around an “8π electrocyclization → carbene → bond cleavage” sequence, the reliability of the manuscript’s conclusions depends on demonstrating that sequence rather than only producing products. In the main text and SI, the authors do not provide kinetic, stereochemical (torquoselectivity), crossover, trapping, or computational evidence that would discriminate this pathway from alternatives. As a result, the mechanistic framing risks being an over-interpretation of product outcomes rather than a supported conclusion. This weakens both the paper’s validity (mechanistic correctness) and the robustness of its conclusions.\n\"As shown in Fig. 1 d, we speculated that the metal-catalyzed 5-endo-annulization of pyridine-alkyne might form zwitterionic vinyl metal species … that might resonate to become a reactive conjugated 8π electronic system and a metal carbene…\" \nThe authors explicitly describe their mechanism as speculative (“we speculated… might…”), yet the Abstract later presents the same pathway as a defining “key characteristic,” creating a mismatch between conjecture and claimed finding. In contemporary synthetic methodology, speculative mechanisms are acceptable when clearly labeled and when the core claims do not rely on them; here the mechanism is used to justify “divergent” downstream bond-cleavage reactivity. The text does not identify which experimental observations uniquely require an 8π electrocyclization (as opposed to stepwise cyclizations) or uniquely require a metal-carbene intermediate (as opposed to vinyl-metal/cationic intermediates). The only mechanistic section in the SI reports reaction execution and yields for labeled experiments, but does not report quantitative isotope incorporation or rate effects that would connect to a specific rate-determining C–H cleavage or pericyclic step. Without such discrimination, the mechanistic proposal should remain explicitly tentative and should not be used as a main evidentiary pillar. This directly impacts how credible the manuscript’s interpretation is.\n\"Deuterated experiment: … residue was purified … to afford the 2a in 91% yield as yellow amorphous solid.\" \nThis labeled-substrate experiment is presented as a mechanistic study, but the description reports only an isolated yield and not the decisive mechanistic readout (e.g., whether deuterium is retained, lost, scrambled, or shows a kinetic isotope effect). If α-C–H cleavage at a defined position is truly “triggered by metal carbene,” then the fate of that hydrogen/deuterium is a key diagnostic and should be reported as a measurable outcome (D incorporation/retention percentages and/or KIE). Reporting only product yield does not test whether the proposed C–H cleavage occurs, which step it corresponds to, or whether it is rate-determining. This makes the mechanistic section insufficient to support the specific mechanistic claims highlighted in the Abstract and Introduction. It also prevents readers from evaluating alternative proton-transfer or exchange pathways. Consequently, the mechanistic conclusions remain under-evidenced.\n\"Control experiment: … dried toluene (1.0 mL) and D2O (0.2 mL) … to afford the 2a'' in 53% yield as yellow amorphous solid.\" \nRunning the reaction with D2O can demonstrate the presence of exchangeable positions or protonation steps, but by itself it does not establish a metal-carbene intermediate or an 8π electrocyclization. The manuscript does not report where deuterium is incorporated, to what extent, or whether incorporation depends on catalyst identity, temperature, or additives; these are the details that would connect D2O effects to a concrete mechanistic inference. Moreover, D incorporation can arise from multiple mechanistic manifolds (e.g., reversible protonation/deprotonation of cationic intermediates), so it is not a unique signature of carbene-induced C–H insertion/cleavage. The relatively large drop in yield (to 53%) could also reflect catalyst inhibition or phase effects, which further complicates interpretation without additional controls. Because the authors use this limited set of experiments as their mechanistic support, the mechanism remains ambiguous. That ambiguity undermines the strength of the manuscript’s mechanistic narrative.\n\"Furthermore, the proposed mechanistic rationale for these cascade reactions is strongly supported by both control experiments and theoretical calculations.\" [[1]](#ref1)\nThis statement exemplifies a common standard in the field for supporting complex cascade mechanisms involving distinct intermediates: a combination of targeted control experiments and theory to validate pathway feasibility and selectivity. By contrast, the reviewed paper proposes a multi-event cascade with an 8π electrocyclization and a metal-carbene intermediate but provides only minimal isotope-related experiments without quantitative mechanistic outputs, and no computations. The gap is especially important because pericyclic-vs-stepwise alternatives often require computational comparison of barriers and/or diagnostic experiments to distinguish. The cited work also illustrates that “control experiments” are typically designed to answer specific mechanistic questions (e.g., source of atoms, pathway selectivity), not merely to show that the reaction still gives product. The reviewed paper’s mechanistic evidence does not reach this bar for the specificity of its mechanistic claims. Therefore, the literature indicates the paper should either supply stronger mechanistic validation or temper its mechanistic conclusions.\n\"However, DFT calculations revealed that the anionic aza 8π-electrocyclization is more favorable than the proposed 7-endo-dig mechanism.\" [[2]](#ref2)\nThis quote shows that even when an 8π electrocyclization is a plausible pathway, distinguishing it from common stepwise cyclization alternatives (here, 7-endo-dig) can require computational evidence. The reviewed paper similarly frames its key ring-forming step as an 8π electrocyclization, but it does not present computational comparisons or decisive experimental probes that would rule out stepwise cyclizations under metal catalysis. The point is not that DFT is mandatory in every case, but that strong mechanistic claims about pericyclic pathways benefit from either calculations or equivalent discriminatory experiments. When such evidence is absent, mechanistic assignments should be presented as hypotheses rather than as defining “key characteristics.” Because the reviewed paper uses the 8π step and carbene language as central justification for divergence, the lack of discrimination is a major interpretive weakness. This directly impacts the credibility of the mechanistic conclusions.\n\"Copper-carbene [Tp(x)Cu=C(Ph)(CO2Et)] and copper-diazo adducts [Tp(x)Cu{η(1)-N2C(Ph)(CO2Et)}] have been detected and characterized in the context of the catalytic functionalization of O-H bonds through carbene insertion by using N2=C(Ph)(CO2Et) as the carbene source. … The relevance of these complexes in the catalytic cycle has been assessed by NMR spectroscopy, and kinetic studies have demonstrated that the N-bound diazo adduct is a dormant species and is not en route to the formation of the copper-carbene intermediate.\" [[5]](#ref5)\nThis abstract highlights what “support” for a copper–carbene intermediate can look like in practice: direct detection/characterization of candidate copper–carbene and related adducts, coupled with kinetic/NMR evidence about their role in the catalytic cycle. The reviewed paper, in contrast, invokes a “metal carbene species” as the trigger for α-C–H/α-C–C cleavage but does not provide direct observation, trapping, or kinetics that would connect an identifiable carbene to the product-forming step. The point is not that all systems must allow spectroscopic detection of the intermediate, but that strong claims about a specific intermediate benefit from targeted evidence beyond product yields. This comparison underscores that the reviewed paper’s mechanistic evidence does not rise to the level typically used to justify a metal–carbene assignment when that assignment is central to the conceptual framing. Without analogous experimental validation (or computational substantiation), the carbene claim remains tentative. That tentativeness should be reflected in the paper’s conclusions and wording.\n\nReferences:\n[1] [Shen, W.-B. et al. “Divergent synthesis of N-heterocycles via controllable cyclization of azido-diynes catalyzed by copper and gold.” *Nature Communications* (2017).](https://pmc.ncbi.nlm.nih.gov/articles/PMC5701061/)\n[2] [Amiri, O. & Bazgir, A. “Anionic aza 8π-electrocyclization as an unprecedented pathway versus 7-endo-dig: DFT study …” *Phys. Chem. Chem. Phys.* (2024).](https://pubs.rsc.org/en/content/articlelanding/2024/cp/d4cp02458c)\n[5] [Pereira, A. et al. “Copper-Carbene Intermediates in the Copper-Catalyzed Functionalization of O–H Bonds.” *Chemistry – A European Journal* (2015).](https://pubmed.ncbi.nlm.nih.gov/26014686/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|77|GPT|2", "source": "prb", "split": "test", "paper_id": "prb77", "comment": "This paper claims “stereo-controlled” late-stage modification of pharmaceuticals, but it does not report stereochemical outcomes (e.g., diastereomeric ratios, enantiomeric ratios/excess, or absolute-configuration assignment for newly formed stereocenters) for the late-stage modification examples, making the stereocontrol conclusion unsupported.\n\n\"The stereo-controlled late-stage modification of some complicated pharmaceuticals indicated the versatility of this protocol.\" \nThis sentence asserts stereocontrol as an achieved feature and uses it as evidence of method “versatility.” Stereocontrol is a quantitative claim: it requires reporting which stereoisomer(s) form and in what proportions, and ideally how stereochemistry was assigned. The paper’s main text does not provide diastereomeric ratios (dr), enantiomeric excess/ratio (ee/er), or chiral analytical data for the late-stage modification products. In late-stage settings, where complex substrates often contain stereocenters and reactive intermediates can be planar (e.g., cationic), stereochemical outcomes are not predictable without measurement. Without those measurements, readers cannot verify whether the transformation is stereocontrolled, stereorandom, or substrate-dependent. Therefore, the conclusion drawn from these examples is not adequately supported.\n\"The different marketed pharmaceuticals, including structurally complicated Gemfibrozil, Idometacin, Estrone, Riluzole, and Candesartan cilexetil, accessing divergent products (**4t**−**4x**) with satisfactory yields.\" \nThis passage describes the late-stage modification experiments but only discusses that products were accessed with “satisfactory yields.” It does not mention stereochemical purity, isomer ratios, or how any stereochemical assignment was performed, despite the fact that these complex molecules can plausibly generate mixtures upon formation of new stereogenic centers. Even if the stereochemistry of the pharmaceutical fragment is retained, the newly formed bond(s) in the modification step can introduce additional stereochemical complexity, which should be reported to substantiate any “stereo-controlled” claim. In methodology papers, it is standard to specify whether late-stage products are single isomers, diastereomer mixtures, or racemates, and to provide the analytical basis for that statement. Because the manuscript omits this information, the reader cannot assess stereoselectivity or stereochemical integrity. This makes the “stereo-controlled” framing unreliable as a conclusion. The paper should either provide the missing stereochemical data or remove/qualify the claim.\n\"According to the procedure B, compound **4v** was obtained as a yellow amorphous solid in 46% yield; **¹H NMR (400 MHz, CDCl₃)** …\" \nThis SI example illustrates the reporting pattern for late-stage-modification products: yields and standard spectroscopic characterization are provided, but stereochemical outcome metrics are not. For a stereocontrol claim, NMR alone (without explicit integration/diagnostics for diastereomers, chiral chromatography, or comparison to authentic standards) is usually insufficient to establish stereoisomeric composition in complex scaffolds. The SI also does not state whether 4v (and analogous 4t–4x) were obtained as single diastereomers, mixtures, or racemates at any new stereogenic center(s). Moreover, the absence of dr/er reporting prevents comparing stereoselectivity across substrates, which is often the key question in late-stage demonstrations. As a result, the SI does not provide the necessary evidence to support the “stereo-controlled” conclusion. This undermines the reliability of a highlighted claim in the Abstract.\n\"Configurational Isomer Mixtures: For reporting the compositions, enantiomeror diastereomer ratios are preferred over enantiomeric or diastereomeric excess values.\" [[3]](#ref3)\nThis guideline makes explicit that when stereoisomer mixtures are possible, authors are expected to report stereoisomeric compositions (er/dr or equivalent), not merely provide structural characterization and yields. The reviewed paper claims stereocontrol but does not report any er/dr for its late-stage-modification products, so its reporting does not meet this community expectation for substantiating stereochemical claims. The guideline also underscores that stereochemical reporting is not an optional detail when stereochemistry is part of the paper’s conclusions. In addition, providing dr/er enables independent readers to interpret whether stereocontrol is robust or incidental. Because the reviewed paper omits these measurements, readers cannot validate the stereocontrol claim. This weakens the paper’s conclusions about the method’s stereochemical performance.\n\"The advent of modern C–H functionalization chemistries has enabled medicinal chemists to consider a synthetic strategy, late stage functionalization (LSF), which utilizes the C–H bonds of drug leads as points of diversification for generating new analogs.\" [[4]](#ref4)\nThis widely cited review emphasizes that late-stage functionalization is used to generate new analogs from drug leads and thus is often evaluated on selectivity and fidelity on complex structures. When authors highlight late-stage applications, the expectation is that critical selectivity dimensions—including stereochemical outcomes when relevant—are made transparent because they affect downstream utility in SAR and medicinal chemistry workflows. The reviewed paper uses late-stage pharmaceutical examples as a headline demonstration but does not provide stereochemical selectivity information while simultaneously claiming stereocontrol. This creates a mismatch between the claimed level of control and the disclosed data needed to support that level of control. In medicinal chemistry contexts, unreported stereoisomer mixtures can materially change biological properties and complicate follow-up synthesis. Therefore, the lack of stereochemical reporting is not cosmetic; it limits how the late-stage results can be interpreted and used. This undermines the reliability of the paper’s late-stage conclusions.\n\"We define LSF as a desired chemical transformation on a complex molecule, without the necessity for a preinstalled functional group that exclusively serves the purpose to enable the transformation.\" [[6]](#ref6)\nThis definition emphasizes that late-stage functionalization is valued because it operates directly on complex molecules, where selectivity limitations (including stereochemical outcomes) often determine practical usefulness. In such settings, stereochemical mixtures can be particularly problematic because they complicate purification and confound downstream structure–activity interpretation, so claims of stereocontrol should be supported by explicit composition measurements. The reviewed paper uses late-stage pharmaceutical examples to argue medicinal-chemistry advantages, but it does not provide the stereochemical evidence required to evaluate whether the transformations are controlled or produce mixtures. Even if the transformation is not intended to be enantioselective, reporting whether single diastereomers or mixtures are obtained is essential when the paper claims stereocontrol. Without that information, the reader cannot judge whether the method genuinely offers controlled diversification on complex substrates or merely yields isolable mixtures. Therefore, the manuscript’s stereocontrol conclusion is not supported at the level implied by its late-stage framing.\n\nReferences:\n[3] [ACS Publications. “Organic Letters — Author Guidelines” (Last updated: Nov 24, 2025).](https://researcher-resources.acs.org/publish/author_guidelines?coden=orlef7)\n[4] [Cernak, T. et al. “The medicinal chemist's toolbox for late stage functionalization of drug-like molecules.” *Chemical Society Reviews* (2016).](https://pubs.rsc.org/en/content/articlelanding/2016/cs/c5cs00628g)\n[6] [Max Planck Institute for Kohlenforschung (Ritter group). “Late-Stage Functionalization” (web page).](https://www.kofo.mpg.de/647198/late-stage-functionalization)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|77|GPT|3", "source": "prb", "split": "test", "paper_id": "prb77", "comment": "This paper provides inconsistent information about the copper catalyst used for the α-C–H cleavage/cascade cyclization (CuTc vs CuTe), which prevents unambiguous reproduction of the key transformation and raises concerns about the reliability of the reported optimization and scale-up.\n\n\"Among them, CuTc was used to produce the cyclization product with the highest yield (96%) (Table 1, entry 9).\" \nThe main text identifies CuTc as the optimal catalyst and ties the reported high yield directly to that specific catalyst. In catalytic cascade chemistry, the identity of the metal salt (counterion/ligand environment) can be decisive for activity and selectivity, so an unambiguous catalyst specification is essential. Because this statement is part of the optimization narrative, any later discrepancy about catalyst identity directly affects whether the optimization can be trusted and repeated. If CuTc is indeed required, a different copper salt (or a misidentified one) could lead to different outcomes or failure. Therefore, consistency of catalyst naming across the manuscript and SI is not a minor editorial detail—it is core experimental information. The later inconsistency in the SI creates uncertainty about what was actually used. This uncertainty undermines reproducibility and the credibility of the reported yields.\n\"The freshly prepared 1 (0.05 mmol, 1.0 equiv.), CuTc (10.0 mol%), and toluene (1.0 mL) were added …\" \nThe Methods section again specifies CuTc, reinforcing that CuTc is the intended catalyst for the general procedure. Because these general procedures are what readers use to reproduce the work, any mismatch with the SI is a major obstacle for replication. The paper also uses short reaction times (0.5 h) and elevated temperature, where catalyst identity can influence decomposition pathways; thus even small differences in catalyst formulation matter. This quote also shows that the paper expects readers to follow these general conditions rather than infer catalyst identity from a table image. When the SI then uses a different catalyst abbreviation, the manuscript ceases to provide a single authoritative procedure. This makes independent reproduction uncertain. As a result, methodological transparency is compromised.\n\"The freshly prepared 1 (0.05 mmol, 1.0 equiv.), CuTe (10.0 mol%), and toluene (1.0 mL) were added …\" \nIn the Supporting Information, the corresponding general procedure (Procedure A) lists “CuTe” rather than “CuTc.” These abbreviations represent different chemical identities, and without clarification the reader cannot know which is correct. Because the SI is the primary location for experimental details and replication, an inconsistency here is particularly damaging to reproducibility. The same SI also uses “CuTe” in the gram-scale procedure, meaning the ambiguity propagates to the scale-up claim as well. Even if this is a typographical or transcription error, the manuscript does not provide a correction or definition to resolve it. Therefore, a key experimental parameter is left ambiguous. This ambiguity materially affects whether the reported chemistry can be reproduced.\n\"New procedures should be fully described in detail to ensure reproducibility.\" [[3]](#ref3)\nThis author-guideline statement captures a standard expectation for method papers: experimental details must be sufficiently precise that another laboratory can repeat the work. The reviewed paper’s inconsistent catalyst specification violates this expectation because the catalyst is a defining component of the method and directly affects outcomes. In practical replication, ambiguity between CuTc and CuTe forces guesswork and can lead to irreproducible results or wasted effort. The issue is especially important here because the paper positions the Cu-catalyzed pathway as a high-yielding, optimized route (up to 96%), making accurate reproduction central to evaluating the method’s utility. The guideline thus supports the view that this inconsistency is a significant methodological flaw rather than a minor wording issue. Resolving it (by defining the catalyst and using one consistent identifier throughout) is necessary for reproducibility.\n\nReferences:\n[3] [ACS Publications. “Organic Letters — Author Guidelines” (Last updated: Nov 24, 2025).](https://researcher-resources.acs.org/publish/author_guidelines?coden=orlef7)", "reviewer_type": "ai", "label": "error", "error_type": "Unstated statement", "label_origin": "expert+llm-filter"}
{"id": "prb|77|GPT|4", "source": "prb", "split": "test", "paper_id": "prb77", "comment": "This paper relies on single-crystal X-ray diffraction to confirm key structures, but the provided crystallographic reports for at least some compounds explicitly state that structure factors were not supplied, which prevents full validation checks and weakens the evidentiary basis for structural confirmation.\n\n\"…the expected NCPC product **2a** was formed with a 31% yield … and its structure was confirmed by X-ray single crystal diffraction analysis.\" \nThe manuscript treats X-ray diffraction as definitive support for the identity of the newly formed NCPC scaffold, which is appropriate when crystallographic data are complete and independently verifiable. Because the NCPC skeleton is central to the paper’s novelty, the strength of the structural evidence matters for the paper’s validity. However, the manuscript’s broader structural claims rely on more than one crystal structure (e.g., for 2z and 3a in the SI). If some of those structures cannot be fully validated due to missing structure factors, the evidentiary strength becomes uneven across key exemplars. This matters because the paper also infers other structures from NMR “by analogy,” using the crystallographic exemplars as anchors. Therefore, incompleteness in crystallographic validation undermines confidence in the structural assignments beyond a single compound. The structural evidence should be provided in a form that allows full checking.\n\"To confirm the structure of the products, a single crystal X-ray structure of product **2z** was obtained, and the structure of other products was deduced from their NMR spectra.\" \nThis sentence makes the crystallographic determination of 2z an explicit cornerstone for broader structural inference (“other products was deduced”). That increases the importance of having fully validated crystallographic data for 2z because it functions as an exemplar for the series. If the X-ray dataset for 2z is incomplete or cannot be fully checked, then the downstream “deduced” assignments become less secure. In other words, the paper’s structural argument has a dependency chain: exemplar X-ray structures → broader assignment by NMR. The SI checkCIF output indicates the 2z crystallographic checking was limited by missing structure factors, which weakens the exemplar. Without structure factors, third parties cannot assess refinement quality and potential issues that could affect atom connectivity or disorder modeling. This makes the structural confirmation less robust than implied.\n\"You have not supplied any structure factors. As a result the full set of tests cannot be run.\" \nThis statement appears in the checkCIF/PLATON report for 2z and indicates that essential data (structure factors) needed for a complete validation were not provided in the submitted crystallographic package. Without structure factors, many diagnostic tests for model quality and data consistency cannot be performed, limiting the ability of reviewers/readers to independently assess the structure. The paper nevertheless uses the crystal structure as confirmatory evidence for key products, which assumes that full validation is possible. While it is possible that structure factors exist elsewhere (e.g., in a separate deposition), the materials provided here do not permit complete checking, and the manuscript does not explain this gap. This is significant because crystallography is being used as a primary line of evidence for structural novelty. Therefore, the structural evidence as presented is incomplete.\n\"All Crystallographic Information Files (CIFs), structure factor tables, and CheckCIF reports must be submitted to The Cambridge Crystallographic Data Centre (CCDC) prior to manuscript submission.\" [[3]](#ref3)\nThis guideline clarifies the community expectation that crystallographic claims should be supported by deposited CIFs together with structure factor tables and checkCIF information. The checkCIF reports in this submission explicitly state that structure factors were not supplied for some structures, meaning the provided crystallographic package does not meet the completeness implied by this guideline. Because the reviewed paper uses crystallography to validate central structural claims, incomplete deposition/availability of structure factors weakens methodological transparency and independent verifiability. The guideline also indicates that structure factors are not optional add-ons but part of the required crystallographic record. Incomplete crystallographic data hinders rigorous peer review of the structural claims. Therefore, this is a significant issue affecting reproducibility and confidence in the reported structures.\n\"Authors are required to deposit structure factor tables with CCDC alongside their CIFs.\" [[3]](#ref3)\nThis sentence is a direct requirement that addresses exactly the deficiency flagged in the checkCIF reports (“You have not supplied any structure factors”). If the authors did not include structure factors in the materials provided to reviewers/readers (or if they were not deposited/linked properly), then the crystallographic evidence is not presented in a fully checkable form. That undermines the strength of “confirmed by X-ray” statements because confirmation in crystallography relies on verifiable refinement against observed data. In addition, because the paper uses X-ray exemplars to support assignment of many other products by NMR, any uncertainty in these exemplars propagates. The guideline thereby supports treating missing structure factors as a major methodological shortcoming, not a peripheral omission. To resolve this, the manuscript should ensure structure factors are available and that the checkCIF reports correspond to fully supplied datasets.\n\nReferences:\n[3] [ACS Publications. “Organic Letters — Author Guidelines” (Last updated: Nov 24, 2025).](https://researcher-resources.acs.org/publish/author_guidelines?coden=orlef7)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|77|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb77", "comment": "The paper contains significant inconsistencies between the compound definitions in Table 1 (and presumably the main text) and the characterization data in the Supplementary Information.\n\n\"1f, R = 4-Br-Ph\"\nThis is the definition of compound **1f** in Table 1 of the Supplementary Information (line 58). It clearly states that **1f** corresponds to the 4-bromophenyl substituted substrate.\n\"Compound 1f was obtained as a yellow liquid; ... 2-((tert-butyldimethylsilyl)oxy)-5-(4-fluorophenyl)pent-4-en-2-yn-1-yl)-6-vinylpyridine\"\nThis is the characterization data for compound **1f** in the Supplementary Information (line 408). It explicitly identifies **1f** as the 4-fluorophenyl derivative, contradicting the definition in Table 1.\n\"1d, R = 4-F-Ph\"\nThis is the definition of compound **1d** in Table 1 of the Supplementary Information (line 52). It states that **1d** corresponds to the 4-fluorophenyl substituted substrate.\n\"Compound 1d was obtained as a yellow liquid; ... 2-((tert-butyldimethylsilyl)oxy)-5-(p-tolyl)pent-4-en-2-yn-1-yl)-6-vinylpyridine\"\nThis is the characterization data for compound **1d** in the Supplementary Information (line 403). It identifies **1d** as the p-tolyl derivative, contradicting the definition in Table 1. These systematic mismatches make it impossible to verify the identity of the synthesized compounds and undermine the reproducibility of the results.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|77|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb77", "comment": "The authors propose an \"8π electrocyclization\" as the key step for forming the 7-membered ring, but this claim is not supported by computational studies or detailed kinetic data.\n\n\"The key characteristics included the formation of a seven-membered ring by the 8π electrocyclization of various alkenes and aromatic heterocycles as π-components\"\nThis sentence from the abstract highlights the \"8π electrocyclization\" as a central claim of the paper. However, the formation of a 7-membered ring via an 8π electrocyclization pathway is non-trivial, as 8π electrocyclizations typically yield 8-membered rings (e.g., from octatetraenes) or bicyclic systems (e.g., from cyclooctatrienes) [1].\n\"To understand this mechanism and elucidate some specific processes of the reaction, several control experiments were conducted. First, the deuterated starting material 1a' was exposed to the standard conditions. The NMR spectra showed that the reaction generated product 2a rather than the deuterated product 2a' ... indicating that the intramolecular 1, 2-hydride shift triggered by metal carbene was not involved in the process.\"\nThe authors rely on deuterium labeling experiments to support their mechanism. While these experiments effectively rule out an intramolecular 1,2-hydride shift, they do not provide direct evidence for the proposed electrocyclization step. Without computational support (e.g., DFT calculations) to verify the feasibility and transition state of the 8π electrocyclization to a 7-membered ring, the proposed mechanism remains speculative.\n\"Electrocyclization reactions can be driven by heating and are not affected by external conditions. However, the reactivity of metal carbene is closely related to the reaction system.\"\nThe authors invoke general principles of electrocyclization but do not demonstrate that their specific system follows these principles. The lack of computational validation is a significant omission for a paper claiming a novel reaction pathway as a key feature.\n\nReferences:\n[1] Liu, L., Du, L. & Li, B. Recent advances in 8π electrocyclization reactions. *Chem. Commun*. **59**, 670−687 (2023). https://pubs.rsc.org/en/content/articlelanding/2023/cc/d2cc04805a", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|77|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb77", "comment": "Benzene as n-component are not good functional groups in typical electrocyclization reactions. In most of the reported electrocyclization reactions, the electron-rich aromatics are far more reactive than those benzene as well as their analogues. However, I suggest the authors do additional trials to investigate the possibilities for the involvement of benzene. Typically, the metal carbene intermediate may also trigger intramolecular 1,2-alkyl migration. In this reaction the ring enlargement products by the releasing of the strain of three membered ring were detected? These results will be important and should be discussed in the manuscript.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|77|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb77", "comment": "Some mistakes should be corrected in text and SI. For example, the \"wittig regent\" should be corrected into \"wittig reagent\" in SI.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|77|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb77", "comment": "Could the metal carbene be directly captured by nucleophilic reagents when the propargyl position is a quaternary carbon rather than a three-membered ring?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|77|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb77", "comment": "For the deuterated experiment of 1a', Where has deuterium atom gone? The author should give some explanation.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|77|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb77", "comment": "What is the diastereoisomer ratio for the substrate 3? Is it a single diastereoisomer? Its relative configuration and dr value should be confirmed.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|77|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb77", "comment": "When the NaOAc were used as nucleophilic reagents, the NaOH as a side product should be generated. It may be unamiable for reaction time or the yield. Have you tried acetic acid as nucleophilic reagent.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|77|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb77", "comment": "The DDQ oxidized side-chain rather than the single bond of core tricycle skeleton. What reason causes this chemoselectivity? The result should be discussed in the manuscript.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|77|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb77", "comment": "Water as proton donor participated in the reaction process. How to control the amount of water? The detail should be described in the manuscript or SI.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|77|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb77", "comment": "The heteroaromatic ring as a n-component participated in the final cyclization. Can benzene ring participate in the cyclization process? The corresponding reaction should be investigated and the result should be putted in manuscript.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|77|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb77", "comment": "The title of figure 4a need be revised, because it is not a deuterium experiment but a reaction of deuterated substrate.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|78|Claude|1", "source": "prb", "split": "test", "paper_id": "prb78", "comment": "The paper overstates the compatibility of electron-donating groups in the 1,3-difunctionalization reaction. The abstract and introduction claim that \"a wide variety of arylcyclopropanes with electron-donating and electron-withdrawing groups could be converted to the 1,3-difunctionalized molecules,\" which is misleading because electron-donating groups (–OMe, –SMe, –OPh, –NHBoc) are explicitly incompatible with the 1,3-difluorination transformation, which is the main focus of the paper.\n\n\"A wide variety of arylcyclopropanes with electron-donating and electron-withdrawing groups could be converted to the 1,3-difunctionalized molecules\" (Abstract)\nThis statement implies broad compatibility across all three transformations (1,3-difluorination, 1,3-oxyfluorination, and 1,3-dioxygenation). However, the substrate scope section clearly states that electron-donating groups are NOT amenable for the 1,3-difluorination reaction, which constitutes the largest substrate scope table in the paper (Figure 2). The claim is thus not representative of the actual scope limitation of the primary transformation.\n\"However, Arylcyclopropanes with electron-donating groups (such as –OMe, SMe, OPh, and NHBoc) were not amenable in this transformation (for more details, see Supplementary Fig. 3).\" (Results section, Substrate scope for 1,3-difluorination)\nThis statement directly contradicts the broad claim made in the abstract. The 1,3-difluorination reaction, which represents the majority of the substrate scope (35 examples in Figure 2), cannot tolerate common electron-donating groups. Only the 1,3-dioxygenation reaction (7 examples in Figure 4) shows compatibility with electron-donating substituents (-OMe, -OPh), yet this represents a minor portion of the overall work.\n\"The protocol exhibits good functional group tolerance and can be performed on gram scale. Various electron-withdrawing groups (e.g., SO2Me, CO2Me, CF3) can be incorporated into the aromatic ring, however, arylcyclopropanes containing electron-releasing aromatic substituents (e.g., OMe, SMe) were not tolerated.\" (from a 2024 review article on the same work, [1])\nIndependent scholarly review of this work confirms that electron-donating groups are indeed a limitation for the fluorination reactions. The claim in the abstract is overly optimistic and does not accurately reflect the scope limitations of the methodology.\n\nReferences:\n[1] McMillan, A. E. et al. Electrochemical deconstructive functionalization of arylcycloalkanes. *Chem. Commun.* **60**, 9598–9619 (2024). https://pubs.rsc.org/en/content/articlehtml/2024/cc/d4cc03279a", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|78|Claude|2", "source": "prb", "split": "test", "paper_id": "prb78", "comment": "The paper reports that electron-withdrawing group-substituted arylcyclopropanes require up to 35.8 F mol⁻¹ of electricity (versus the theoretical 2 F mol⁻¹ for a two-electron oxidation), representing Faradaic efficiencies below 10%. This significant loss of energy efficiency is not discussed or rationalized, which represents a major gap in understanding the practical applicability of the method.\n\n\"Isolated yield = 52%, 27% starting material was recovered, electricity = 23.9 F mol⁻¹\" (SI, compound 16)\nFor the protected amide substrate 16, which achieves 52% yield, the electricity consumption of 23.9 F mol⁻¹ is approximately 12 times the theoretical requirement of 2 F mol⁻¹. This corresponds to a Faradaic efficiency of only ~4.3% (calculated as 2 × 0.52 / 23.9 × 100%). Such low efficiency is not discussed in the main text, yet it has significant implications for the sustainability and scalability claims of electrochemistry.\n\"Isolated yield = 82%, electricity = 35.8 F mol⁻¹\" (SI, compound 34, protected sugar derivative)\nThe protected sugar derivative 34 requires 35.8 F mol⁻¹ of electricity. Even with 82% yield, this corresponds to a Faradaic efficiency of only ~4.6%. The paper emphasizes the scalability and green chemistry advantages of electrochemistry, but the high energy consumption undermines these claims. Standard practice in electrochemical methodology papers is to report and discuss Faradaic efficiency [2].\n\"The Faradaic efficiency (n), or current efficiency, describes how many of the electrons transferred into the reaction mixture end up in the product... This is an effective way to compare reactions with different electron equivalents.\" (from [3])\nBest practices in electrochemistry recommend reporting Faradaic efficiency as a key metric. The present paper omits this important parameter from discussion, making it difficult to assess the practical efficiency of the transformation and compare it with alternative methods.\n\nReferences:\n[2] Grim, R. G. et al. Reliable reporting of Faradaic efficiencies for electrocatalysis research. *Nat. Commun.* **14**, 4180 (2023). https://pmc.ncbi.nlm.nih.gov/articles/PMC9977834/\n[3] Pletcher, D. et al. Making electrochemistry easily accessible to the synthetic chemist. *Green Chem.* **22**, 6217–6228 (2020). https://pubs.rsc.org/en/content/articlehtml/2020/gc/d0gc01247e", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|78|Claude|3", "source": "prb", "split": "test", "paper_id": "prb78", "comment": "The proposed mechanism involves a two-step anodic oxidation: first, arylcyclopropane to radical cation, and then benzyl radical to benzyl cation. While trapping experiments support the existence of both benzyl radical and benzyl cation intermediates, there is no direct evidence that the second oxidation occurs at the anode rather than through alternative pathways (e.g., homogeneous electron transfer, disproportionation).\n\n\"Different from thermochemical and photochemical conditions, benzyl radical can further lose one electron at anode and be converted to benzyl carbonium under electrochemical conditions.\" (Introduction)\nThis mechanistic claim is central to distinguishing the electrochemical approach from other methods. However, the mechanistic studies (Figure 6) only demonstrate: (1) the oxidation potential of starting materials via CV, (2) DFT calculations of the radical cation, (3) radical trapping with O2 and BrCCl3, and (4) cation trapping via Ritter reaction in CH3CN. None of these experiments directly establish that the benzyl radical is oxidized heterogeneously at the anode surface.\n\"The detection of the oxygenation products highly proposed the formation of the benzyl radical during the reaction... Furthermore, the electrolysis of phenylcyclopropane and Et₃N∙3HF in CH₃CN resulted in isolation of amidation product, which suggest the involvement of benzyl carbonium intermediate during the reaction.\" (Discussion, Mechanistic studies)\nWhile these trapping experiments successfully demonstrate the presence of both radical and cation intermediates, they do not distinguish between heterogeneous electron transfer at the electrode surface versus homogeneous electron transfer or radical disproportionation to generate the cation. A divided cell experiment comparing anode and cathode compartments, or cyclic voltammetry of a model benzyl radical precursor, would provide more definitive evidence [4].\n\"Based upon this, and related published literature, the authors proposed that the arylcyclopropane undergoes anodic oxidation to generate a radical cation, which participates in a three-electron nucleophilic attack by fluoride... Further anodic oxidation would access a benzylic carbocation\" (from [1])\nExternal reviewers have also noted that the second anodic oxidation step is proposed rather than proven. Standard mechanistic rigor for electrochemical transformations would include measurement of the oxidation potential of the benzyl radical intermediate or use of redox mediators to probe the second oxidation step.\n\nReferences:\n[1] McMillan, A. E. et al. Electrochemical deconstructive functionalization of arylcycloalkanes. *Chem. Commun.* **60**, 9598–9619 (2024). https://pubs.rsc.org/en/content/articlehtml/2024/cc/d4cc03279a\n[4] Francke, R. & Little, R. D. Redox catalysis in organic electrosynthesis: basic principles and recent developments. *Chem. Soc. Rev.* **43**, 2492–2521 (2014). https://pubs.rsc.org/en/Content/ArticleLanding/2014/CS/c3cs60464k", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|78|Claude|4", "source": "prb", "split": "test", "paper_id": "prb78", "comment": "The paper positions itself as expanding on Shono's 1970 work on anodic oxidation of arylcyclopropanes, but the comparison is limited to stating that Shono \"only\" reported six examples. The paper does not adequately discuss what new mechanistic understanding it provides beyond Shono's established radical cation mechanism or why the electrochemical approach was not further developed for 50 years.\n\n\"Pioneering work was disclosed by Shono and coworkers who reported anodic oxidation of arylcyclopanes in methanol. But only six examples were presented in this report.\" (Introduction)\nThe comparison with Shono's work focuses solely on the number of examples (6 vs. 57 in this work) rather than providing a substantive analysis of what limited the original methodology or what mechanistic insights the current work provides. Shono's 1970 paper also reported the anodic oxidation of arylcyclopropanes in methanol to generate 1,3-dimethoxy ethers via a radical cation mechanism [5], which is fundamentally the same mechanistic pathway proposed here.\n\"In a seminal early report (1970), Shono reported the anodic oxidation of arylcyclopropanes in methanol... a selection of arylcyclopropanes with different substituents, both on the aromatic ring and on the cyclopropane scaffold, underwent ring opening to form 1,3-dimethoxyether products in good yields and with high faradaic efficiencies.\" (from [1])\nExternal analysis of this work notes that Shono's original work actually achieved \"high faradaic efficiencies\" for the 1,3-dioxygenation reaction. The present paper does not discuss why its Faradaic efficiencies are substantially lower for the fluorination reactions, or what specific advances in understanding are provided beyond changing the nucleophile from methanol to Et3N·3HF.\n\"Cyclopropane ring-opened products were obtained in the anodic oxidation of some arylcyclopropanes in methanol. Controlled potential oxidation and product studies suggest the intermediacy of cation radicals.\" (from Shono & Matsumura, J. Org. Chem. 1970 [5])\nShono's original work already proposed the radical cation mechanism that this paper reiterates. While the use of Et3N·3HF as a fluoride source and the expanded substrate scope represent practical advances, the mechanistic framework remains largely unchanged from the 1970 precedent. The paper would benefit from a more thorough discussion of what new mechanistic understanding is gained.\n\nReferences:\n[1] McMillan, A. E. et al. Electrochemical deconstructive functionalization of arylcycloalkanes. *Chem. Commun.* **60**, 9598–9619 (2024). https://pubs.rsc.org/en/content/articlehtml/2024/cc/d4cc03279a\n[5] Shono, T. & Matsumura, Y. Organic Synthesis by Electrolysis. VI. Anodic Oxidation of Arylcyclopropanes. *J. Org. Chem.* **35**, 4157–4160 (1970). https://pubs.acs.org/doi/10.1021/jo00837a604", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|78|GPT|1", "source": "prb", "split": "test", "paper_id": "prb78", "comment": "This paper makes mechanistic and scope-relevant inferences from cyclic voltammetry (CV) onset potentials, but the CV methodology uses an aqueous Ag/AgCl reference electrode in acetonitrile without reporting calibration to an internal standard (e.g., Fc/Fc+), which undermines the validity and interpretability of the reported oxidation potentials and the resulting mechanistic conclusion about substrate oxidizability.\n\n\"Cyclic voltammetry was performed in a three-electrode cell. The working electrode was a Pt electrode, the counter electrode a graphite rod. The reference was an Ag/AgCl electrode submerged in saturated aqueous KCl solution. CH<sub>3</sub>CN (10 mL) containing 0.5 mmol \\\"Bu<sub>4</sub>NBF<sub>4</sub> was tested as blank background. The cyclic voltammogram of cyclopropanes (10 mM) were recorded at room temperature in an electrolyte of \\\"Bu<sub>4</sub>NBF<sub>4</sub> (50 mM) in MeCN. The scan rate is 100 mV/s.\"\nThis sentence states that an aqueous Ag/AgCl (sat. KCl) reference is directly interfaced to a nonaqueous MeCN electrolyte during CV. In nonaqueous electrochemistry, aqueous-reference/non-aqueous-sample interfaces are well-known to introduce significant liquid junction potentials and potential drift, and can also contaminate the nonaqueous electrolyte with water and chloride. Because the paper does not describe any salt-bridge design, junction mitigation strategy, or reference calibration, the numerical potentials reported from these CVs cannot be assumed to be accurate on an absolute scale. This is especially consequential here because the CV is used to rationalize why arylcyclopropanes are accessible while alkyl cyclopropanes are not. Even if qualitative trends might remain, the manuscript presents absolute onset values and uses them as mechanistic support without documenting the necessary referencing controls.\n\"In contrast, arylcyclopropanes even with strong electron withdrawing group (-NO₂) have relatively lower oxidative potential (E\\<sub\\>onset\\</sub\\> = 1.68 V for **1** and E\\<sub\\>onset\\</sub\\> = 1.99 V for **1a**). These results illustrate that aryl group is important for the oxidation of the cyclopropane substrates.\"\nThis passage relies on CV-derived onset potentials to support a key mechanistic argument about the role of aryl substitution in enabling anode oxidation. However, the paper does not specify the potential scale (e.g., vs Ag/AgCl in what medium) in the main text, nor does it report any conversion to a standard nonaqueous reference scale such as Fc/Fc+. Without a stable and standardized reference, onset potentials (which are themselves method-dependent) are not directly comparable to literature values and can shift substantially with junction potential and reference drift. The conclusion “aryl group is important” may still be chemically plausible, but the presented numerical evidence is not robust enough to justify the strength of the inference. In current organic electrochemistry practice, authors typically report potentials referenced to Fc/Fc+ (or provide a clear calibration) precisely to make such claims interpretable across setups. The manuscript’s current reporting makes it difficult to assess whether the potential differences cited are intrinsic to the substrates or artifacts of the reference arrangement.\n\"Abstract -Thisreport recommends that the redox couples ferrocene/\nferriceniuxn ion Lferrocene : bis(r —cyclopentadienyl )iron(II )]and\nbis(biphenyl)chromium(I)/bis(biphenyl)chrornium(O) be employed as\nreference redox systems.\" [[1]](#cite-1)\nThis IUPAC recommendation directly contrasts with the manuscript’s choice to report CV potentials without anchoring them to a recommended reference redox system. The key point is not that Ag/AgCl can never be used, but that nonaqueous potential reporting should be tied to a reference redox couple to enable meaningful comparison and reproducibility. The paper’s mechanistic section reports Eonset values as if they were broadly interpretable, yet it does not provide an Fc/Fc+ calibration or similar procedure. Because the authors are using CV as mechanistic evidence (not merely as a qualitative diagnostic), adherence to recommended reporting practice becomes important for the validity of the mechanistic support. The IUPAC text underscores that standardized redox systems (like Fc/Fc+) exist specifically to address these comparability issues. As written, the manuscript does not show that its CV potentials satisfy these recommended conditions.\n\"Quite frequently electrode potentials have been reported versus aqueous\nreference electrodes such as the calomel electrode, the silver—silver chloride electrode or\nthe standard hydrogen electrode in water. Many of the experimental arrangements that have\nbeen employed included liquid junction potentials.\" [[1]](#cite-1)\nThis passage highlights a well-established methodological pitfall: reporting nonaqueous electrochemical potentials against aqueous reference electrodes often entails uncontrolled liquid junction potentials. The manuscript’s CV description matches this pitfall closely, because it places an aqueous Ag/AgCl (sat. KCl) reference in a MeCN system and then reports onset potentials numerically. Junction potentials can be large and sensitive to solvent composition, electrolyte identity, temperature, and frit condition; this can create shifts that are comparable to (or larger than) the potential differences used for mechanistic inference. Because the paper does not demonstrate junction stability (e.g., via an internal standard measured in the same CV) or provide conversion to a recognized redox reference scale, the reported Eonset values are not adequately justified. This directly affects the credibility of the mechanistic narrative built on those values. Therefore, the mechanistic interpretation should be weakened or the electrochemical methodology/reporting strengthened.\n\"All of the more common reference electrodes discussed in textbooks, such as the silver chloride (Ag/AgCl) or calomel (Hg/Hg2Cl2) reference electrodes, are based on aqueous chemistry and are not well suited for use with non-aqueous solvents.\" [[2]](#cite-2)\nThis external guidance summarizes a key reason the manuscript’s CV setup is problematic: aqueous reference electrodes introduce compatibility and stability issues when used with nonaqueous test solutions. The manuscript’s CV section does not acknowledge these issues, nor does it describe protective measures (e.g., double junction, matched solvent in the reference compartment, or rigorous calibration). Because the mechanistic section depends on CV potentials to argue about oxidizability across substrates, the suitability of the reference electrode is not a minor implementation detail but central to the reliability of the evidence. The quote also connects to practical consequences relevant here, such as leakage of reference filling solution components into the nonaqueous cell, which can perturb both the electrochemistry and the measured potentials. In other words, the concern is not theoretical; it can materially affect the CV traces and their interpretation. Without addressing this, the manuscript’s CV-derived numerical claims remain insufficiently supported.\n\"The potential of a pseudo-reference electrode must be established indirectly, usually by adding an electrochemically active “internal standard” compound to the test solution. The well-behaved ferrocene/ferrocenium redox couple is one of the more popular internal standards.\" [[2]](#cite-2)\nThis quote describes a widely used mitigation strategy for nonaqueous potential reporting: calibrating against an internal redox standard such as Fc/Fc+. The manuscript does not report adding ferrocene (or any internal standard) to its CV measurements, nor does it report any calibration procedure, yet it reports onset potentials and uses them in mechanistic reasoning. Without internal-standard referencing, it is hard to distinguish real substrate-dependent shifts from reference drift or junction-potential artifacts. Importantly, the absence of such calibration prevents readers from mapping the reported Eonset values onto commonly used potential scales and comparing them to related arylcyclopropane oxidation literature. This undermines reproducibility, because other groups cannot straightforwardly confirm whether they are operating in the same electrochemical regime. Adding a simple Fc/Fc+ calibration (or reporting potentials vs Fc/Fc+) would materially strengthen this part of the paper. As-is, the CV evidence does not meet common reporting expectations for nonaqueous electrochemistry.\n\"it is interesting to note that if the solvent polarity is lowered, a high liquid junction potential drift will form at the aqueous/non-aqueous interface, rendering the Ag|AgCl|KCl (saturated)|frit reference electrode redox potential unstable\" [[3]](#cite-3)\nThis statement provides a concrete mechanistic reason why an aqueous Ag/AgCl reference can yield unstable potentials in nonaqueous environments: junction potential drift at the aqueous/non-aqueous interface. The manuscript’s CV setup explicitly creates such an interface (aqueous KCl reference vs MeCN electrolyte) and does not report controls to confirm stability over the measurement period. If the reference potential drifts, then reported onset potentials can shift between runs or even within a run, which directly compromises the numerical Eonset values used to support mechanistic conclusions. This is particularly relevant because the paper compares substrates and emphasizes differences on the order of a few tenths of a volt, a range that can be affected by junction issues. The quote also implies that even if an aqueous reference is stable in some polar solvents under some conditions, this stability is conditional and should be demonstrated, not assumed. The manuscript currently does not demonstrate that condition. Therefore, the CV-based mechanistic support should be treated as unreliable until appropriately referenced and validated.\n\nReferences:\n[1] [G. Gritzner and J. Kuta, “Recommendations on reporting electrode potentials in nonaqueous solvents (Recommendations 1983)”, *Pure and Applied Chemistry* 56 (1984) 461–466.](http://iupac.org/publications/pac/pdf/1984/pdf/5604x0461.pdf)\n[2] [Pine Research, “Referencing Electrochemical Data to an Internal Standard” (Support Article, 2024).](https://pineresearch.com/support-article/reference-to-an-internal-standard/)\n[3] [Pine Research, “Non-Aqueous Reference Electrode Overview” (Support Article, 2024).](https://pineresearch.com/support-article/non-aqueous-reference-electrode-overview/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|78|GPT|2", "source": "prb", "split": "test", "paper_id": "prb78", "comment": "This paper concludes that the protocol is broadly compatible (including electron-withdrawing substituents) and scalable, but the supplementary experimental records show that several representative substrates require extremely high charge passed (up to 23.9 F mol−1) while giving only moderate yields and sometimes substantial starting-material recovery, which indicates low electron utilization (low Faradaic efficiency) and undermines the paper’s conclusions about practicality and scalability under electrochemical conditions.\n\n\"This protocol has good functional groups tolerance and can be scaled up.\"\nThis claim asserts practicality as a major advantage of the method, and it is presented in the abstract as a headline contribution. In preparative electrosynthesis, “scalable” and “practical” are tightly coupled to how much charge must be passed per mole of product, because charge directly controls time, energy consumption, and electrode wear at scale. If many substrates require an order-of-magnitude excess of charge relative to the nominal electron stoichiometry, scale-up becomes substantially less attractive even if the chemistry is feasible. The manuscript does not qualify its scalability claim by distinguishing “easy” substrates from those that require very high charge. The SI, however, provides the quantitative electricity values needed to assess this point and shows large variability. Therefore, the abstract’s broad framing overstates the generality of the scalability/practicality advantage.\n\"Arylcyclopropanes with electron-withdrawing groups (such as ester, amide, acetyl, cyano, nitro and aldehyde groups) were also amenable, furnishing the desired products in 42–56% yields by prolonging the reaction time (**14**–**20**), although these substrates have higher oxidative potential.\"\nThis sentence presents electron-withdrawing-group (EWG) compatibility as a central scope claim, attributing lower yields primarily to longer required electrolysis time. However, in electrochemistry, “prolonging time” at constant current is equivalent to passing substantially more charge, which can strongly affect energy efficiency and side reactions. The main text does not quantify how much additional charge is required for these EWG substrates, which is an important part of assessing practical compatibility. When the SI data are examined, some EWG-containing substrates require dramatically more charge than the parent substrate, suggesting substantial unproductive current consumption. This affects the robustness of the conclusion that EWG substrates are broadly “amenable” in a practically meaningful sense. The paper would be stronger if it explicitly reported and discussed charge/Faradaic efficiency across the scope rather than focusing on time alone. As written, the scope claim is not adequately contextualized by the electron economy revealed in the SI.\n\"NMR Yield = 75% using 1-fluoronaphthalene as internal standard, electricity = 2.4 F mol⁻¹.\"\nThis SI entry establishes that for the parent substrate, the transformation can proceed at a relatively modest charge (2.4 F mol−1) with high yield, consistent with a reasonably efficient electrolysis. It provides a useful baseline showing that the system can operate near a few Faradays per mole on at least one substrate. This baseline matters because the paper uses it to support claims of practicality and scale-up potential. However, the same SI section also reports substrates requiring far higher charge for comparable or worse yields, indicating that the efficiency is not general across the claimed scope. The manuscript does not highlight this disparity or analyze its implications for scalability. In electrochemical synthesis, such substrate-dependent swings in charge demand are often a decisive factor for adoption. Therefore, the baseline efficiency for (2) does not justify broad practicality claims without addressing the outliers.\n\"Isolated yield = 52%, 27% starting material was recovered, electricity = 23.9 F mol\\(^{-1}\\).\"\nThis SI entry shows that for at least one scope example, the electrolysis consumes an extremely large amount of charge (23.9 F mol−1) while still leaving significant starting material unreacted and giving only moderate yield. Passing ~24 F mol−1 is roughly an order of magnitude higher than the few Faradays often associated with efficient 1–2 electron organic electrosyntheses, and it strongly suggests that a large fraction of current is diverted to side processes (e.g., solvent/electrolyte decomposition, product degradation, or competing electrode reactions). Starting-material recovery at such high charge further implies that simply “pushing more electrons” does not linearly translate to productive conversion, raising concerns about electrode fouling or mass-transport/overpotential limitations under the chosen conditions. This is a major practical limitation because it directly impacts throughput and energy cost, especially on scale. The main text’s phrasing (“amenable” by prolonging time) obscures this degree of inefficiency. Without an explicit discussion of Faradaic efficiency and why these high-charge cases occur, the paper’s broad scope/practicality conclusions are not fully reliable.\n\"Isolated yield = 49%, electricity = 23.9 F mol\\(^{-1}\\).\"\nThis is a second independent example where an electron-poor substrate requires 23.9 F mol−1 to reach only ~50% isolated yield, reinforcing that the high-charge issue is not an isolated anomaly. Because the paper positions electron-withdrawing substituents as a key advantage over prior photo/oxidant-based approaches, the electron efficiency for such substrates is central to the claimed significance. A method that technically produces product but requires ~24 Faradays per mole to do so may be less compelling in practice than a method that achieves similar outcomes with near-stoichiometric charge. The manuscript does not provide Faradaic efficiencies, cell voltage profiles, or side-product analyses that would help readers understand where the extra charge is going. Without that, readers cannot evaluate whether the inefficiency is intrinsic (e.g., high overpotential driving competing reactions) or fixable by optimization. This gap meaningfully affects the reliability of the paper’s practical conclusions. Therefore, the EWG “compatibility” claim should be qualified by these charge demands.\n\"A Faraday (F) is the amount of charge carried by one mole of electrons and is equal to 96,485 Coulombs (C). The Shono oxidation is a 2e− reaction. Therefore, a minimum of 2 Faradays per mole of substrate are needed to convert all the substrate to product.\" [[5]](#cite-5)\nThis external source provides a clear benchmark for interpreting the manuscript’s reported electricity values: for a 2-electron process, 2 F mol−1 is the theoretical minimum to fully convert substrate to product. While the reviewed paper’s mechanism may not be exactly the Shono oxidation, its reported charges can still be meaningfully assessed against the general principle that Faradays per mole reflect electron stoichiometry and efficiency. When the SI reports 23.9 F mol−1 for incomplete conversion and ~50% yield, it indicates that the electrolysis is operating far from the theoretical minimum, implying substantial inefficiency. Such inefficiency directly impacts scale-up because the needed electrolysis time and energy scale with charge. The benchmark helps demonstrate that the issue is not merely “longer time,” but quantitatively extreme excess charge. It also clarifies why reporting and discussing electron economy is part of evaluating electrosynthetic practicality. Therefore, the manuscript’s broad scalability framing is not aligned with the electron-accounting reality shown in its own SI.\n\"The Faradaic efficiency (n), or current efficiency, describes how many of the electrons transferred into the reaction mixture end up in the product.\" [[4]](#cite-4)\nThis definition underscores why the SI’s very large Faradays-per-mole values are not a minor optimization detail but a core methodological limitation. If many electrons do not end up in product, the process loses one of electrochemistry’s touted advantages: using electrons as a “clean reagent” with minimal waste. The reviewed manuscript emphasizes catalyst-free and oxidant-free conditions and highlights scalability, both of which are commonly associated with favorable electron economy. However, the SI’s high-charge cases strongly suggest low Faradaic efficiency for a meaningful subset of the claimed scope. The paper does not calculate or report Faradaic efficiencies, nor does it explain likely competing electrode reactions that consume charge. This omission makes it hard to assess whether the method is generally efficient or only efficient for a subset of substrates. As a result, the conclusions about practicality and the claimed advantage over prior approaches should be substantially qualified.\n\nReferences:\n[4] [C. Schotten et al., “Making electrochemistry easily accessible to the synthetic chemist”, *Green Chemistry* 22 (2020) 3358–3375 (Open Access).](https://pubs.rsc.org/en/content/articlehtml/2020/gc/d0gc01247e)\n[5] [S. L. Goes et al., “Exploring Electrosynthesis: Bulk Electrolysis and Cyclic Voltammetry Analysis of the Shono Oxidation”, *J. Chem. Educ.* 99 (2022) 3242–3248 (PMC full text).](https://pmc.ncbi.nlm.nih.gov/articles/PMC9580565/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|78|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb78", "comment": "The paper presents the electrochemical 1,3-dioxygenation of arylcyclopropanes as a novel contribution without adequately acknowledging that this specific transformation (anodic oxidation in methanol to form 1,3-dimethoxy compounds) was reported by Shono et al. in 1970.\n\n\"Here we developed electrochemical C-C bond cleavage and 1,3-difuntionalization of arylcyclopropanes... 1,3-dioxygenation of arylcyclopropanes were achieved with a highly chemo- and regioselectivity by the strategic choice of nucleophiles.\"\nThis statement implies that the 1,3-dioxygenation (specifically methoxylation) is a new development by the authors. However, the reaction conditions (anodic oxidation in methanol) and products (1,3-dimethoxy compounds) are essentially identical to those reported by Shono et al. in 1970 [1]. While the authors cite Shono [1] in the introduction as an example of \"rarely developed\" electrochemical C-C bond cleavage, they fail to explicitly state that Shono already achieved the 1,3-dioxygenation reaction, thereby overstating the novelty of this specific part of their work.\n\"Cyclopropane ring-opened products were obtained in the anodic oxidation of some arylcyclopropanes in methanol.\"\nThis quote from the abstract of Shono et al. (1970) [1] confirms that the electrochemical ring-opening of arylcyclopropanes in methanol to yield 1,3-dioxygenated products was established decades ago. The current paper's failure to discuss this direct precedence in the context of their 1,3-dioxygenation results is a significant omission.\n\nReferences:\n[1] Shono, T., & Matsumura, Y. (1970). Organic Synthesis by Electrolysis. VI. Anodic Oxidation of Arylcyclopropanes. *The Journal of Organic Chemistry*, 35(12), 4157–4160. https://pubs.acs.org/doi/abs/10.1021/jo00837a604", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|78|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb78", "comment": "The paper inaccurately claims that benzyl radicals cannot be converted to benzyl cations under photochemical conditions, contrasting it with electrochemistry. This ignores established photochemical methods that can access carbocation intermediates via oxidative quenching or radical oxidation.\n\n\"Different from thermochemical and photochemical conditions, benzyl radical can further lose one electron at anode and be converted to benzyl carbonium under electrochemical conditions.\"\nThis statement presents a false dichotomy between electrochemical and photochemical methods. While direct anodic oxidation is a powerful way to generate cations, photochemical methods can also generate benzyl cations from benzyl radicals through single-electron transfer (SET) using appropriate photocatalysts or oxidants [2, 3]. For instance, photoirradiation of certain precursors or the use of strong photooxidants can lead to the formation of benzyl cations, enabling similar reactivity. The claim that this pathway is unique to electrochemistry (\"Different from... photochemical conditions\") is scientifically inaccurate and ignores relevant literature.\n\"For the bromides, the benzyl cation intermediates were generated through oxidation of the corresponding benzyl radicals.\"\nThis quote from a 2018 study [3] demonstrates that benzyl cations can indeed be generated from benzyl radicals under photochemical conditions, directly contradicting the paper's assertion that this transformation is unique to electrochemical methods.\n\nReferences:\n[3] Mizuno, K., et al. (2018). Substituents Have a Large Effect on Photochemical Generation of Benzyl Cations. *Chemistry – A European Journal*, 24(15), 3742-3746. https://chemistry-europe.onlinelibrary.wiley.com/doi/abs/10.1002/chem.201705929", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|78|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb78", "comment": "The paper characterizes yields of 42-56% for electron-withdrawing group (EWG) substituted arylcyclopropanes as \"good\" and \"amenable\", which is an overstatement. While potentially better than some historical failures, these yields are moderate and limit the practical utility of the method for these substrates.\n\n\"Arylcyclopropanes with electron-withdrawing groups (such as ester, amide, acetyl, cyano, nitro and aldehyde groups) were also amenable, furnishing the desired products in 42–56% yields by prolonging the reaction time (**14**–**20**)...\"\nThe authors describe these yields as \"amenable\" and imply successful application. However, yields in the range of 40-50% are generally considered moderate in synthetic methodology. While the authors note the difficulty due to high oxidative potential, characterizing these results as \"good\" (implied by the context of \"amenable\" and \"good functional groups tolerance\" in the abstract) is misleading. A more objective assessment would describe these yields as moderate or limited.\n\"The electron-withdrawing group substituted arylcyclopropanes resulted in low yields (less than 30%) of the desired products.\"\nThis quote from a recent related study [4] suggests that while 42-56% is an improvement over <30%, it still represents a significant challenge. The paper should contextualize its yields more accurately rather than broadly claiming \"good functional groups tolerance\".\n\nReferences:\n[4] Wang, H., et al. (2023). Electrochemical Oxidation Enables Regioselective 1,3-Hydroxyfunctionalization of Cyclopropanes. *Organic Letters*, 25(33), 6158–6162. https://pubs.acs.org/doi/10.1021/acs.orglett.3c02309", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|78|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb78", "comment": "The anodic ring opening of arylcyclopropanes using methanol as nucleophile was described by Shono in the 1970s (J. Org. Chem. 1970, 35, 4157). The authors must know this early work, as it has been cited as reference 50 in the manuscript. However, the citation is misplaced and the work by Shono has not been properly acknowledged in the introduction.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|78|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb78", "comment": "It is important that the authors properly describe and acknowledge the work by Shono in the introduction. This should include an appropriate description in the text and also in Figure 1, which should include the early anodic cyclopropane ring opening example and the reference.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|78|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb78", "comment": "Some of the isolated products seem to contain high amounts of impurities according to the NMR spectra (e.g., compound 8 contains solvent). The authors should either provide cleaner spectra or, if some product is difficult to dry because it is volatile, the NMR purity should be mentioned.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|78|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb78", "comment": "Some numbers in Figures 6a and 6b are difficult to see. The quality might be improved.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|78|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb78", "comment": "The substrate scope of the difluorination reaction seems rather limited. The authors mainly showed that electron-withdrawing groups could be tolerated under the reaction conditions, but the compatibility of electron-donating groups with this method has not been demonstrated. Could methoxy groups and other EDGs be tolerated on the phenyl rings in these reactions? In addition, only one heterocycle example (thiophene) was shown in Figure 2. Could other six-membered and five-membered heterocycles such as pyridines, pyrimidines, furans, pyrroles, etc. be tolerated under this difluorination conditions?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|78|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb78", "comment": "1. Another concern I have about these reactions is the synthetic utilities. The authors have shown that the difluorination reactions could be applied on the natural product scaffold. Yet, these examples are just simple attachment of a phenylcyclopropanes to natural products that do not have complex functional groups. The structures of these natural products might look large, but they not contain any complex functional groups.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|78|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb78", "comment": "It is unnecessary to separate the large-scale synthesis in a single table, which only contains four substrates. The authors should consider combining these data in Fig 2. – Fig. 4\n\nThis is also the case for Figure 4, which described the scope of di-methoxylation of phenyl-cyclopropanes with only 7 examples. The author should consider combining Fig 3 and Fig. 4 in one Figure.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|78|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb78", "comment": "It is interesting that cyclic ethers could also be used in the reactions for the construction of C-O bonds. The authors proposed a possible mechanism in the supporting information, but no evidences were provided to support the proposed mechanism. It is interesting that dimethoxymethane led to the formation of non-fluorinated product, while the other two ethers formed the fluorinated products. The authors should explain this result.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|78|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb78", "comment": "The yields of most products are moderate. What are the side products? Is the low yield due to the lower conversion of the starting materials or due to the formation of other side products?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|78|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb78", "comment": "The authors conducted cyclic voltammetry studies to explain the requirement of the phenyl groups on the cyclopropane rings for these reactions. Two onset potentials (without mentioning the reference electrodes in the main text) have been reported by the authors for two of the phenyl-cyclopropanes. However, it is very confusing how the authors were able to get these onsite potential data from the CV data.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|78|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb78", "comment": "The supporting information seems satisfactory and it is clear from the NMR spectra that these compounds could be isolated in high purity. In addition, the authors have provided detailed protocols, with pictures, for the set-up of the small-scale electrochemical reactions.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|78|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb78", "comment": "Could the authors also show the set-up, with pictures, of the large-scale synthesis? In addition, the resolution of the NMR spectra seems low and it is hard to see the splitting pattern of many HNMR spectra.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|78|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb78", "comment": "The splitting pattern for the 19F NMR should also be reported. The 13C NMR spectra should not be reported with two significant digits after the comma as it suggests an accuracy that is not met by the current NMR equipment.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|78|Human_2|10", "source": "prb", "split": "test", "paper_id": "prb78", "comment": "High-resolution MS data have been reported for most of the compounds, but some of the compounds, for example, 18, 17, 15, 6, 19... do not have any MS data. Although these compounds have been previously reported, mass data should be reported for these molecules that were synthesized using a different method.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|78|Human_2|11", "source": "prb", "split": "test", "paper_id": "prb78", "comment": "Grammar issues are throughout the entire manuscript; nearly every sentence of this manuscript has certain grammar mistakes. For example, the first sentence: “C-C bonds are the basic skeleton of organic compounds and widely existed in nature, it’s deconstructive functionalization are meaningful” A comma should not be used to connect two complete sentences. The authors are strongly encouraged to have native speakers to polish this manuscript.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|79|Claude|1", "source": "prb", "split": "test", "paper_id": "prb79", "comment": "The paper proposes that cPLA2α regulates transcriptional repression by EZH2 to protect cancer cells, yet provides no direct experimental evidence demonstrating this mechanistic relationship. This central claim is supported only by correlations from gene set enrichment analyses and hierarchical clustering of drug activity profiles, without any biochemical validation of the proposed pathway.\n\n\"Unsupervised hierarchical clustering of the drug correlations revealed an interesting similarity between the action of cPLA2α inhibitors and multiple histone methyltransferase inhibitors (Fig. S3), specifically drugs targeting EZH2, the catalytically active component of the polycomb group repressive complex 2 (PRC2). The finding suggests that cPLA2α may play a novel role in epigenetic silencing of transcription in cancer.\"\nThis finding is based solely on similarity in drug activity profiles across cancer cell lines, which indicates shared cellular vulnerabilities but does not demonstrate that cPLA2α directly regulates EZH2 or PRC2 activity. Similar drug response patterns can arise from many shared downstream effects without requiring a direct mechanistic link between targets. According to established principles in causal inference for biological networks, \"two genes may exhibit a high correlation in expression levels, but this may be driven by a common upstream regulator rather than a direct interaction\" [[1]](#citation-list). The paper does not measure H3K27me3 levels, EZH2 activity, or any direct indicators of PRC2 function following AVX420 treatment.\n\"A direct regulation of epigenetic modifiers by cPLA2α signaling has to our knowledge not been described to date.\"\nThe authors acknowledge that no prior evidence exists for the proposed mechanism, yet proceed to build their central thesis around this correlation-based inference without providing the necessary direct experimental validation. Standard practice for validating such novel mechanistic claims would include measuring EZH2 protein levels or activity, H3K27me3 marks, or demonstrating that genetic perturbation of cPLA2α affects PRC2-dependent transcriptional repression. None of these experiments were performed.\n\"We thus propose that cPLA2α activity regulates transcriptional repression by EZH2 to protect cancer cells that are reliant on fatty acids as an energy source.\"\nThis causal statement is not supported by the evidence presented. The paper shows correlations between cPLA2α inhibitor sensitivity and PRC2 pathway gene signatures, but does not demonstrate that cPLA2α inhibition reduces EZH2 activity or that the observed effects on cell death are mediated through changes in epigenetic repression. According to guidelines on target validation, establishing causality requires demonstrating that \"changes in the target gene directly influence the observed phenotype\" [[2]](#citation-list), which this study does not accomplish for the cPLA2α-EZH2 axis.\n\"mTOR thus presents as the logical connection between cPLA2α and epigenetic suppression by PRC2.\"\nWhile the paper references prior literature suggesting connections between mTOR and EZH2, it provides no experimental evidence that AVX420 treatment affects mTOR signaling or that mTOR mediates the proposed epigenetic effects. The logical chain from cPLA2α→mTOR→EZH2 remains entirely hypothetical without measurements of mTOR phosphorylation status or activity following AVX420 treatment.\n\nReferences:\n[1] [Advances in Causal Inference Methods for Biological Network Analysis](https://bioscipublisher.com/index.php/cmb/article/html/3925/)\n[2] [Target identification and validation in research - World Journal of Biology Pharmacy and Health Sciences](https://wjbphs.com/sites/default/files/fulltext_pdf/WJBPHS-2024-0116.pdf)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|79|Claude|2", "source": "prb", "split": "test", "paper_id": "prb79", "comment": "The paper attributes the ROS-dependent cell death and transcriptional responses to cPLA2α inhibition without providing genetic validation through siRNA knockdown or CRISPR knockout experiments that would confirm target specificity. This is a critical gap given that the mechanism of ROS induction remains unexplained by the authors.\n\n\"While the mechanism behind the increase in iROS in response to cPLA2α inhibition is not directly evident from this data, we showed that the iROS increased rapidly, and in the absence of any transcriptional or translational alterations.\"\nThe authors explicitly acknowledge they do not understand how AVX420 increases intracellular ROS. Without demonstrating that genetic depletion of cPLA2α reproduces the ROS induction phenotype, it is possible that the ROS increase results from off-target effects of the compound rather than from cPLA2α inhibition specifically. This is especially concerning given that chemical inhibitors can have pleiotropic effects. Target validation best practices indicate that \"knockout studies, knockdown studies, and genetic association studies provide evidence of a target's significance\" and are essential for \"causality determination\" [[2]](#citation-list).\n\"AVX420 treatment induced a dose-dependent increase in iROS in both cell lines (Fig. 5e). The response occurred within 30 min, peaked at 8-12 hours, and preceded the loss of cell viability\"\nThe rapid ROS induction (within 30 minutes) is attributed to AVX420 treatment, but without siRNA/shRNA knockdown or CRISPR knockout of PLA2G4A showing similar ROS increases, there is no evidence this effect is cPLA2α-dependent. According to established drug target validation protocols, \"the failure of concordance between siRNA and inhibitor studies... has important implications in biology\" [[3]](#citation-list), and genetic validation is considered essential to distinguish on-target from off-target effects.\n\n* Quote from literature: \"Using both pharmacological and genetic approaches, we identified that cPLA2α is involved in cervical cancer growth and survival... To further confirm the significant role of cPLA2α in chemoresistance, we conducted cPLA2α knockdown using two siRNAs that specifically target different regions of cPLA2α.\" [[4]](#citation-list)\nThis quote from a related study on cervical cancer demonstrates the standard practice of validating cPLA2α as a target using both pharmacological and genetic approaches. The current paper under review lacks this critical validation step, particularly for the novel claims about ROS-dependent cell death in acute leukemia cells. While the authors cite their previous work on multiple myeloma which included some siRNA data, the specific mechanism of ROS induction and ATF4-target gene activation in T-ALL cells presented as novel findings in this paper is not genetically validated.\n\nReferences:\n[2] [Target identification and validation in research - World Journal of Biology Pharmacy and Health Sciences](https://wjbphs.com/sites/default/files/fulltext_pdf/WJBPHS-2024-0116.pdf)\n[3] [Recognizing and exploiting differences between RNAi and small-molecule inhibitors](https://pmc.ncbi.nlm.nih.gov/articles/PMC2924165/)\n[4] [Inhibition of cytosolic phospholipase A2 alpha increases chemosensitivity in cervical cancer](https://pmc.ncbi.nlm.nih.gov/articles/PMC6605985/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|79|Claude|3", "source": "prb", "split": "test", "paper_id": "prb79", "comment": "The paper claims that AVX420 \"has the potential to treat acute leukemias,\" yet provides no in vivo efficacy data in leukemia animal models. All anticancer efficacy data are derived from cell line experiments, which is insufficient to support therapeutic claims given the well-documented challenges in translating in vitro findings to clinical relevance.\n\n\"Our study suggests AVX420 has the potential to treat acute leukemias, and other cancers with specific adaptations to a high ROS burden.\"\nThis therapeutic claim is made based solely on cell line viability data from T-ALL and AML cell lines (CCRF-CEM, Jurkat E6.1, MV-4-11, HL-60). The paper does not include any xenograft models, patient-derived xenograft (PDX) models, or other in vivo systems to validate efficacy. Given that the authors' own previous work with AVX235 included in vivo efficacy studies in breast cancer xenografts and arthritis models, the absence of similar validation for the acute leukemia claims represents a significant gap in supporting the therapeutic potential claim.\n\"GK420 (AVX420), was selected as the lead compound based on high potency and selectivity in vitro and ex vivo.\"\nWhile the compound demonstrates in vitro potency and selectivity, and ex vivo effects on eicosanoid production in blood samples, the translation to in vivo anticancer efficacy for leukemia has not been demonstrated. This contrasts with the standard established by other cPLA2α inhibitor studies cited in the paper, such as ASB14780 which \"reduced AA levels and inhibited the growth of triple-negative breast cancer xenografts,\" and the authors' own previous work showing AVX235 efficacy in murine cancer models. Without in vivo data, the therapeutic potential claim for acute leukemias remains speculative.\n\"In other cancers where cPLA2α has prognostic significance e.g., lung cancer, acute myeloid leukemia and glioblastoma, synthetic cPLA2α inhibitors have been shown to suppress cancer cell or tumor growth and in preclinical models of ovarian and cervical cancers were effective sensitization agents for radiation or chemotherapy.\"\nThe authors acknowledge that other cPLA2α inhibitors have been validated in preclinical models for various cancers, establishing in vivo validation as the expected standard in the field. The paper claims to have \"uncovered a highly sensitive potential susceptibility of acute leukemias to cPLA2α inhibition,\" but this significant discovery is not validated in vivo, limiting the strength of the therapeutic conclusion.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|79|Claude|4", "source": "prb", "split": "test", "paper_id": "prb79", "comment": "While the paper proposes that AVX420 induces cell death through reactivation of ATF4 target genes via loss of EZH2-mediated repression, the RNA-seq and Ribo-seq data explicitly show no evidence of the classical integrated stress response (ISR) pathway activation, yet the paper does not provide sufficient experimental evidence to support the proposed alternative mechanism.\n\n\"While these findings supported the hypothesis that AVX420 initiated cell death via the ATF4 dependent ISR pathway, the absence of translational repression, or selective upregulation of ATF4 translation in response to AVX420, would strongly argue against this, and an alternative mechanism for activation of ATF4 target genes is more likely.\"\nThe authors correctly identify that their Ribo-seq data showing no differential ribosomal occupancy argues against the classical ISR mechanism. However, they then propose an alternative mechanism involving EZH2-mediated transcriptional repression without directly testing it. They do not measure whether AVX420 treatment affects H3K27me3 levels at ATF4 target gene promoters, does not show changes in EZH2 binding or activity, and does not demonstrate that EZH2 knockdown mimics the transcriptional changes induced by AVX420.\n\"Given our findings showing a correlation between PRC2 activity and sensitivity to cPLA2α inhibition, we instead propose that cPLA2α could be important for maintaining H3K27 trimethylation-dependent transcriptional suppression of certain ATF4 target genes for example ATF3, which was upregulated by AVX420 and is indeed known to be repressed by PRC2.\"\nWhile ATF3 is cited as being \"known to be repressed by PRC2,\" the paper does not verify whether H3K27me3 marks at the ATF3 promoter are altered following AVX420 treatment. The reference citations support that ATF3 can be repressed by PRC2 in general contexts, but the specific claim that cPLA2α inhibition leads to loss of this repression is not demonstrated. Standard practice would involve ChIP-qPCR or ChIP-seq for H3K27me3 at target genes following treatment.\n\"An alternative mechanism for upregulation of DDIT3 (CHOP) could involve L3MBTL2-AS1, an RNA that was upregulated at 6 hours, which has been shown to downregulate the expression of L3MBTL2, a transcriptional repressor of DDIT3 (CHOP).\"\nThe authors present multiple potential mechanisms for the transcriptional changes without experimentally distinguishing between them. This suggests that the mechanistic basis for the observed transcriptional response remains unclear, weakening the conclusion that the proposed EZH2/PRC2 mechanism is responsible for AVX420's anticancer effects.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|79|GPT|1", "source": "prb", "split": "test", "paper_id": "prb79", "comment": "This paper makes mechanistic claims that cPLA2α inhibition (AVX420) triggers leukemia cell death through loss of mTOR/PRC2 (EZH2/H3K27me3)-dependent transcriptional repression and an ATF4-dependent stress program, but the presented evidence is largely correlational/computational and does not establish causality in the leukemia models.\n\n\"Unsupervised hierarchical clustering of the drug correlations revealed an interesting similarity between the action of cPLA2α inhibitors and multiple histone methyltransferase inhibitors (**Fig. S3**), specifically drugs targeting EZH2, the catalytically active component of the polycomb group repressive complex 2 (PRC2). The finding suggests that cPLA2α may play a novel role in epigenetic silencing of transcription in cancer.\" \nThis is a similarity-of-profiles argument (drug–drug correlation and clustering) rather than a direct measurement of PRC2/EZH2 activity, H3K27me3, or chromatin changes following AVX420. Such analyses can be useful for hypothesis generation, but they are not sufficient to claim that AVX420 functionally converges on PRC2 in the treated leukemia cells. The manuscript does not, in the main text, show biochemical readouts (e.g., EZH2 activity assays) or chromatin assays (e.g., H3K27me3 ChIP-seq) that would directly test the proposed epigenetic step. Without perturbation experiments (e.g., EZH2 inhibition/overexpression, PRC2 component knockdown, or resistant alleles) demonstrating necessity/sufficiency, the “suggests” framing is still used later to support a concrete mechanistic model. Because this mechanism is central to the paper’s “novel function” claim, the lack of causal evidence meaningfully weakens the validity of the mechanistic conclusions.\n\"Given our findings showing a correlation between PRC2 activity and sensitivity to cPLA_{2α} inhibition, we instead propose that cPLA_{2α} could be important for maintaining H3K27 trimethylation- dependent transcriptional suppression of certain ATF4 target genes\" \nThis explicitly grounds the mechanism in correlation and a proposal, rather than direct demonstration that AVX420 decreases H3K27 trimethylation or derepresses PRC2 targets via PRC2 loss-of-function. The paper uses “PRC2 activity” as inferred from gene-set enrichment and overlaps, but does not show that PRC2 marks or PRC2 occupancy change at implicated loci in the AVX420-treated leukemia cells. The leap from enriched signatures to a specific chromatin mark mechanism is substantial, particularly because ATF4 targets can be induced through multiple upstream pathways unrelated to PRC2. The same section argues against canonical ISR translation control, but does not directly test alternative explanations (e.g., transcription factor activation downstream of ROS). As written, the mechanistic chain “cPLA2α → mTOR/PRC2 → H3K27me3 → ATF4-target derepression → death” remains speculative. That makes the paper’s mechanistic novelty claim less robust than standard causal practice in chemical biology.\n\"AVX420 initiates an ATF4-dependent but ISR-independent transcriptional program to initiate cell death.\" \nThe heading states ATF4-dependence, but in the surrounding results the primary support is that several induced genes are described as “established targets of ATF4.” Inferring transcription-factor dependence from target-gene lists is not equivalent to demonstrating dependence, especially when ROS can activate multiple stress-responsive regulators with overlapping target sets. The manuscript does not provide (in the visible Methods/Results) functional perturbations of ATF4 (e.g., knockdown/CRISPR or pharmacologic ISR modulation) showing that AVX420-induced death requires ATF4. Moreover, it does not show ATF4 protein induction, nuclear localization, or DNA binding changes that would support a direct ATF4 mechanism. As a result, the “ATF4-dependent” phrasing overstates what is demonstrated and risks misattributing the proximate death pathway. This is a conclusions issue because the ATF4/ISR framing is used to interpret transcriptomics and connect to the proposed epigenetic model.\n\"Providing one chemical probe for a given protein is also insufficient. Each protein should be targeted by another equally well-characterized ‘orthogonal’ chemical probe having a completely different chemical structure which would reduce the probability of having common off-targets.\" ([1](https://pmc.ncbi.nlm.nih.gov/articles/PMC4706458/))\nThe paper’s central mechanistic claims rely heavily on inhibitor-based phenotypes and on correlations across three inhibitors, but it does not demonstrate that the key downstream epigenetic/ATF4 conclusions hold under orthogonal target validation strategies. While AVX002 is a different chemical class, the manuscript still does not establish that the PRC2/EZH2-linked transcriptional effects and ROS-dependent death are abolished when cPLA2α function is genetically removed or when target engagement is otherwise verified in the sensitive leukemia lines. Chemical-probe best practice emphasizes reducing common off-target explanations via orthogonal probes and appropriate controls; similarity of IC50 patterns alone does not rule out shared liabilities (e.g., redox effects) that could converge on stress pathways. This matters particularly because the paper proposes a “hitherto unexplored function” of cPLA2α in epigenetic adaptation, which requires unusually strong linkage of phenotype to target. The quote highlights that without such orthogonal corroboration, mechanistic inference from small-molecule phenotypes can be misleading. Therefore, the paper’s mechanistic interpretation falls short of common field standards for target-to-phenotype causal attribution.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|79|GPT|2", "source": "prb", "split": "test", "paper_id": "prb79", "comment": "This paper overstates the selectivity of the thiazolyl ketones (including the lead GK420/AVX420) for cPLA2α based on limited counter-screening and on inhibition percentages that show substantial activity on other PLA2 enzymes, undermining the validity of the “selective inhibitor” premise used throughout the biological interpretation.\n\n\"All the new analogs mentioned above can be considered selective inhibitors of cPLA2α, because all present minimal inhibition of GVIA iPLA2 and GV sPLA2 at high concentrations (0.091 mole fraction), as shown in Table 1.\" \nThis sentence makes a strong interpretive claim (“selective inhibitors”) and anchors it to Table 1 values at a single, high mole fraction. However, “minimal inhibition” is not consistent with several of the listed percentages, including substantial inhibition of GV sPLA2 for the lead-like compounds. Because the paper uses selectivity to justify that downstream cellular phenotypes reflect cPLA2α inhibition (rather than PLA2 cross-reactivity), any overstatement here threatens internal validity. Moreover, selectivity over only two other PLA2s does not address broader off-target risks typical for small molecules, but even within this narrow panel the data show non-trivial inhibition. When the premise is “selective,” readers will reasonably infer that cross-family inhibition is negligible across the tested panel, which is not supported by the presented numbers. This mismatch is significant because selectivity is repeatedly used to justify mechanistic conclusions and therapeutic relevance.\n<td>GK420</td>\n  <td>99<br>0.0016 ± 0.0002</td>\n  <td>0</td>\n  <td>46</td>\nFor GK420, Table 1 reports 46% inhibition of GV sPLA2 at the stated high concentration (0.091 mole fraction). A near-half inhibition at a single dose is difficult to reconcile with the phrase “minimal inhibition,” and it suggests that GK420 is not cleanly selective within the reported PLA2 panel. Even if the authors consider 46% “acceptable,” that threshold should be justified, because partial inhibition of another PLA2 could plausibly influence lipid signaling and downstream stress phenotypes. The issue is amplified because the biological conclusions (ROS induction, transcriptional programs, and cell death) are sensitive to perturbations in lipid metabolism and inflammatory mediators. Without a clearer selectivity window quantified across concentrations (e.g., IC50s for iPLA2 and sPLA2), the claim of selectivity remains under-supported. This weakens confidence that AVX420’s cancer-cell phenotypes are attributable specifically to cPLA2α.\n\"Again, α-methyl substituted analogs can be considered selective inhibitors of cPLA2α, because all present minimal inhibition of GVIA iPLA2 and GV sPLA2 at high concentrations (0.091 mole fraction) (Table 1).\" \nThe “again” indicates the authors are extending the same selectivity interpretation to another subset of compounds, reinforcing that selectivity is central to the narrative. However, the α-methyl analogs include compounds with majority inhibition of iPLA2 and/or sPLA2 at the same dose, which contradicts the stated rationale. This is not a cosmetic inconsistency; it suggests a systematic overinterpretation of the counter-screening results. Because these compounds are then used as comparators (e.g., to argue shared cPLA2α-specific sensitivity signals in the CCLS), inflated selectivity claims can propagate into downstream association analyses. In chemical biology, such interpretive inflation is a known source of false mechanistic attribution when compounds have secondary activities. The paper would need either stronger selectivity evidence or more cautious language and additional controls.\n<td>GK439</td>\n  <td>97<br>0.0029 ± 0.0004</td>\n  <td>67</td>\n  <td>53</td>\nGK439 shows 67% inhibition of GVIA iPLA2 and 53% inhibition of GV sPLA2 at the single reported high dose, which is clearly not “minimal.” Even if GK439 is not the lead, the paper’s argument for target-specific commonalities across multiple inhibitors depends on these analogs being functionally selective for cPLA2α. When comparator compounds substantially inhibit other PLA2s, shared sensitivity patterns could reflect shared polypharmacology rather than shared cPLA2α engagement. This is a direct threat to the validity of the CCLS-derived pathway associations claimed to represent “specific to cPLA2α inhibition.” At minimum, these data require dose–response selectivity metrics for iPLA2 and sPLA2 (not just percent inhibition at one condition) before labeling the set “selective.” Without this, the biochemical foundation for downstream claims is weaker than standard expectations.\n\"Only high-quality chemical probes generate meaningful biological data.\" ([1](https://pmc.ncbi.nlm.nih.gov/articles/PMC4706458/))\nThe paper positions AVX420 as a selective tool to uncover a new cPLA2α function, which is exactly the type of situation where chemical-probe quality is decisive. If selectivity is uncertain even within the narrow enzyme family panel, then mechanistic interpretations from phenotypic readouts (ROS, transcriptional changes, death) become ambiguous. The quoted best-practice statement is not about demanding perfection, but about aligning strength of biological claims with strength of probe characterization. Here, the manuscript draws strong mechanistic implications (epigenetic adaptation to ROS) but provides selectivity evidence that is inconsistent with its own “minimal inhibition” wording and lacks broader profiling. This mismatch increases the risk that off-target activities contribute to the observed phenotypes. Consequently, the conclusions about cPLA2α-specific vulnerabilities in acute leukemias are less reliable.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|79|GPT|5", "source": "prb", "split": "test", "paper_id": "prb79", "comment": "This paper applies permissive significance conventions (including treating p<0.1 as a starred result and relaxing gene-level association FDR to 20%), which increases false-positive risk and undermines the robustness of the derived mechanistic associations and pathway narratives.\n\n\"Repeated measures one way ANOVA was performed, followed by Dunnets multiple comparison test between inhibitors and appropriate stimulated control, * indicates p<0.1, ** p<0.05 and *** p<0.01.\" \nMarking p<0.1 with an asterisk signals to readers that these comparisons are being treated as evidence, despite being weaker than conventional thresholds used in biomedical experiments. This is particularly problematic in a setting that already involves multiple comparisons (multiple eicosanoids and multiple inhibitor conditions), where marginal p-values are more likely to arise by chance. The legend also does not clearly define whether and how familywise multiplicity across the many measured analytes was controlled beyond the within-panel Dunnett step, leaving uncertainty about the effective false-positive rate. Because the ex vivo assays are used to support claims of specificity and pathway effects, overemphasizing marginal p-values can lead to overstated confidence. In addition, using a nonstandard “* = p<0.1” convention makes it harder to compare results to typical pharmacology reporting practice. Overall, the statistical reporting here reduces the reliability of the evidentiary base for downstream claims.\n\"Several common associations were found by relaxing the FDR to 20% (Table S5)\" \nRelaxing FDR to 20% explicitly permits a high expected fraction of false discoveries among the reported “discoveries,” which is sometimes acceptable for exploratory analyses but requires cautious interpretation and independent validation. In the manuscript, these relaxed-FDR associations are discussed in the same mechanistic context as the stricter findings (e.g., highlighting EZH2 and transcriptional repressors), which risks readers treating them as comparably reliable. Because the CCLS has modest sample size (56 lines with expression data), relaxed thresholds can yield unstable gene lists that change under small perturbations. The manuscript does not, in the main text, present follow-up experiments validating the relaxed-FDR associations as functional determinants of sensitivity. As a result, the pathway narrative built on these associations is less robust than typical standards for drawing mechanistic conclusions from high-dimensional correlations.\n\"Well-reasoned statistical arguments contain much more than the value of a single number and whether that number exceeds an arbitrary threshold.\" ([5](https://www.amstat.org/asa/files/pdfs/p-valuestatement.pdf))\nThe ASA statement emphasizes that inference quality cannot be reduced to thresholded p-values, particularly when multiple analyses are performed. In this paper, the use of p<0.1 as a starred outcome and the reliance on thresholded associations (including relaxed FDR) increase the chance that results are driven by thresholding choices rather than stable effect patterns. The statement also implicitly highlights the need for full reporting and contextualization (effect sizes, uncertainty intervals, and transparent analysis choices), which are especially important when claims involve screening-derived correlations. Without strong confirmatory experiments, permissive thresholds can inflate the appearance of mechanistic support. This critique is not about demanding p<0.05 everywhere; it is about aligning the strength of the claims with the strength of the statistical evidence and controlling error rates appropriately. The external guidance supports that the manuscript’s thresholding practices weaken the robustness of its conclusions.\n\"It calls for controlling the expected proportion of falsely rejected hypotheses—the false discovery rate.\" ([6](https://www.dcscience.net/Benjamini-Hochberg-1995-FDR.pdf))\nThe original FDR framing makes clear that the chosen FDR level directly corresponds to the expected proportion of false positives among rejected hypotheses. When the manuscript reports associations after “relaxing the FDR to 20%,” it is therefore implicitly accepting that a substantial portion of those associations may be false. This is not inherently wrong for generating hypotheses, but it becomes a major issue when such associations are used to motivate a specific mechanistic model (e.g., epigenetic repression dependencies). Standard practice is to treat high-FDR lists as exploratory and to validate key hits experimentally or in independent datasets. The manuscript does not provide such validation in the main text for the relaxed-FDR associations it highlights. Therefore, the combination of permissive thresholds and mechanistic narrative risks overinterpretation of noisy associations.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|79|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb79", "comment": "The paper proposes a novel mechanism where cPLA2α regulates PRC2-mediated repression, but this is based solely on drug sensitivity correlations and gene set enrichment, without direct biochemical validation.\n\n\"We thus propose that cPLA2α activity regulates transcriptional repression by EZH2 to protect cancer cells that are reliant on fatty acids as an energy source.\"\nThis is a central mechanistic claim of the paper, yet it is supported only by indirect evidence such as drug sensitivity correlations (Fig. 4a) and overlap of differentially expressed genes with BMI1 knockdown (Fig. 6b). The authors do not provide direct biochemical evidence, such as Western blots showing changes in H3K27me3 levels or EZH2 localization upon cPLA2α inhibition, which are standard assays to verify PRC2 activity modulation [1].\n\"Comparing the activity of novel compounds against a reference library of known chemotherapeutics... revealed an interesting similarity between the action of cPLA2α inhibitors and multiple histone methyltransferase inhibitors... specifically drugs targeting EZH2\"\nWhile drug sensitivity profiles can generate hypotheses, they are insufficient to establish a direct regulatory link. The observed correlation could be due to parallel pathways or off-target effects rather than a direct regulation of PRC2 by cPLA2α. Without validating the effect on the catalytic product of PRC2 (H3K27me3), the proposed mechanism remains speculative.\n\nReferences:\n[1] Hojfeldt, J. W. et al. Modulators of Cellular and Biochemical PRC2 Activity. *Harvard DASH*. https://dash.harvard.edu/bitstreams/d20369ad-2c8b-41ba-b26a-b7819b28e73c/download", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|79|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb79", "comment": "The authors claim an \"ATF4-dependent but ISR-independent\" mechanism where ATF4 targets are upregulated without translational activation of ATF4, but they fail to demonstrate increased ATF4 protein levels.\n\n\"We did not identify any transcripts with differential RO, indicating that AVX420 did not affect translation.\"\nThe authors use Ribosome Profiling (Ribo-seq) to rule out translational upregulation of ATF4, which is the canonical mechanism of ATF4 induction during the Integrated Stress Response (ISR). They conclude the mechanism is ISR-independent but still ATF4-dependent. However, they do not show that ATF4 protein levels are actually increased, which is a critical missing piece of evidence.\n\"ATF3 has additional function of stabilizing ATF4 protein.\"\nTo explain how ATF4 targets are upregulated without translational induction, the authors speculate that ATF3 stabilizes ATF4 protein. However, they do not provide a Western blot to demonstrate this stabilization. Since ATF4 is rapidly degraded by the proteasome [2], demonstrating its protein accumulation is essential to support the claim that the pathway is indeed ATF4-dependent.\n\nReferences:\n[2] Lassot, I. et al. Control of Activating Transcription Factor 4 (ATF4) Persistence by Multisite Phosphorylation and Interaction with $\\beta$-TrCP. *Molecular and Cellular Biology* **30**, 5088-5100 (2010). https://pmc.ncbi.nlm.nih.gov/articles/PMC2963346/", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|79|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb79", "comment": "The authors attribute the ROS increase to \"metabolic consequences\" and \"mitochondrial fatty acid oxidation\" without any experimental evidence supporting this metabolic alteration.\n\n\"This favors metabolic consequences... and will require a deeper investigation into the role of cPLA2α in cancer cell fatty acid metabolism to be fully understood.\"\nThe authors admit that the mechanism of ROS generation is not evident from their data but proceed to build a model (Fig. 6d) based on the hypothesis that cPLA2α-derived arachidonic acid serves as a fuel source for fatty acid oxidation (FAO). This is a major gap in the paper's logic.\n\"We propose cPLA2α-derived arachidonic acid is integral to cancer cell survival in this case, both as a fuel source, and for maintaining epigenetic suppression...\"\nThis proposal is entirely speculative. The authors do not measure fatty acid oxidation rates (e.g., using a Seahorse analyzer [3]) or mitochondrial respiration to confirm that the cells are indeed relying on FAO or that cPLA2α inhibition disrupts this process. Attributing the ROS phenotype to a specific metabolic shift without metabolic data undermines the robustness of the conclusions.\n\nReferences:\n[3] Liu, Z. et al. CPT1A-mediated fatty acid oxidation confers cancer cell adaptive resistance to cytolytic immune cells. *Proceedings of the National Academy of Sciences* **120**, e2302878120 (2023). https://www.pnas.org/doi/10.1073/pnas.2302878120", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|79|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb79", "comment": "The paper is titled \"Next Generation... from Synthesis to Chemotherapeutic Mechanism of Action\" and claims GK420 is a \"more potent and selective lead\", yet it lacks in vivo evaluation of this new lead to confirm its chemotherapeutic potential compared to the previous generation (GK470).\n\n\"Here we report... the discovery of a more potent and selective lead, GK420... with significant chemotherapeutic properties.\"\nThe term \"chemotherapeutic properties\" and the \"Next Generation\" label strongly imply an improvement in therapeutic utility. However, the paper only presents in vitro (enzyme assays, cell lines) and ex vivo (blood) data for GK420. The previous generation inhibitor, GK470, was validated in in vivo models [4]. Without in vivo efficacy data for GK420, it is difficult to assess whether the improved in vitro potency translates to better therapeutic potential, which is a key expectation for a \"Next Generation\" study.\n\nReferences:\n[4] Kokotos, G. et al. Inhibition of group IVA cytosolic phospholipase A2 by thiazolyl ketones in vitro, ex vivo, and in vivo. *J Med Chem* **57**, 7523-7535 (2014). https://doi.org/10.1021/jm500192s", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|79|Gemini|5", "source": "prb", "split": "test", "paper_id": "prb79", "comment": "The authors claim GK420 is a \"selective\" inhibitor of cPLA2α, but the data shows significant inhibition of GV sPLA2 (46%) at the tested concentration, and selectivity profiling is limited to only two other PLA2 isoforms.\n\n\"All the new analogs mentioned above can be considered selective inhibitors of cPLA2α, because all present minimal inhibition of GVIA iPLA2 and GV sPLA2...\"\nTable 1 shows that GK420 inhibits GV sPLA2 by 46% at 0.091 mole fraction. Describing nearly 50% inhibition as \"minimal\" is misleading. Furthermore, the human PLA2 superfamily consists of many other groups (e.g., Groups IB, IIA, IID, IIE, IIF, III, X, XII) [5]. Claiming selectivity based on testing against only two other isoforms (GVIA iPLA2 and GV sPLA2) is insufficient to establish the compound as a truly selective cPLA2α inhibitor, especially given the significant off-target activity against GV sPLA2.\n\nReferences:\n[5] Dennis, E. A. et al. Phospholipase A2 enzymes: physical structure, biological function, disease implication, chemical inhibition, and therapeutic intervention. *Chemical Reviews* **111**, 6130-6185 (2011). https://doi.org/10.1021/cr200085w", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|79|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb79", "comment": "The acquisition of crystal structures of protein-ligand complexes is a crucial aspect in the process of structure modification, as it provides essential binding information. Unfortunately, this study is deficient in the availability of pertinent data pertaining to crystal structures.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|79|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb79", "comment": "The directing binding of AVX420 with cPLA2α was not characterized.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|79|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb79", "comment": "In Scheme 1A, the mention of a \"potential increase in plasma stability through the introduction of a methyl group\" did not find support in the subsequent experimental findings. The compound AVX420, used for further studies, exhibits a mere addition of one oxygen atom compared to AVX235. Thus, additional exploration is required to obtain further insights into the optimization of the compound structure.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|79|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb79", "comment": "The authors explain the non-selectivity of compounds with or without α-methyl for GVIA iPLA2 and GV sPLA2 with the same description, \"MINIMAL inhibition\" (on page 8 line 8 and line 16), but note that there is a disparity in inhibition rates between these two classes of compounds (Table 1).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|79|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb79", "comment": "Further pathway experiments and in vivo and PK studies are required to validate the mechanism and ascertain the effects.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|79|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb79", "comment": "Johansen modified the structure of GK470, resulting in the improved activity of compound GK420. The related studies demonstrated that AVX420 induced the apoptosis in tumor cells through upregulation of intracellular oxidative stress response and transcriptional signaling pathways. However, this manuscript was deficient in the crucial animal experiments and pertinent preclinical study, such as pharmacokinetics and bioavailability. Hence, in my opinion, the manuscript did not meet the criteria for publication in Nature Communications.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|79|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb79", "comment": "The new compounds were tested against GV and GVIA recombinant PLA2s using a valid vitro assay, showing a relatively low/minimal level of inhibition for these structurally distinct PLA2s. Nevertheless, given the number of existing PLA2s enzymes in the superfamily it is still possible that the compound inhibits other PLA2 isoforms and even that the inhibition profile for the tested ones is different when used in cells and tissues. Moreover, the compound could inhibit other unrelated enzymes when used in vivo. I wonder if the authors have compared the effects of GK420 (on cellular eicosanoid release and on cancer cell viability/proliferation) with the effects of gene manipulation of cPLA2? Does depletion of cPLA2 result in similar alterations in cell viability, ROS production, eicosanoid generation? This would help strengthen the idea that the identified mechanism of action of the compound in cancer cells is dependent on its selective inhibition of cPLA2.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|79|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb79", "comment": "The authors have convincingly demonstrated that GK420 induces ROS production and cell death in a number of hematological cancer cell lines. They describe the phenotypic and genetic changes leading to cancer cell death. In principle, as the authors state, cPLA2 could promote cancer cell proliferation through the mitogenic action of eicosanoids, such as PGE2. But cPLA2 also has some other functions, not related to lipid mediator production. Does the mechanism of action of GK420 on cancer cells depend on its capacity to inhibit cPLA2-induced AA release coupled with lipid mediator generation and signalling?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|79|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb79", "comment": "Combining their own screening data with available datasets the authors found links between the action of cPLA2 and epigenetic regulation. I wonder if genetic manipulation of cPLA2 in some of the identified sensitive cell lines would lead to alterations of the epigenetic mechanisms as predicted by these in silico analyses? It would also be very interesting to see if this potential epigenetic control is linked with the cPLA2-AA signaling axis or perhaps with other cPLA2 functions not related to lipid mediator signalling.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|79|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb79", "comment": "Correlations between cPLA2 inhibitor activity and gene expression data suggested that cPLA2-induced cancer cell death is linked with the induction of oxidative stress and that the resistance to the inhibitor could be mediated by Nrf2 signaling. Have the authors tried to target Nrf2 in combination with cPLA2 genetic manipulation in representative resistant vs sensitive cell lines to confirm the suggested mechanism? Does cPLA2 inhibition induce ER stress and alter Nrf2 signaling in relevant cell models? Do these events precede the measured rise in oxidative stress? Similarly, an important added value to this work would be if the authors could connect the dots between cPLA2 and ATF4, PRC2/mTOR signaling by cellular mechanistic studies using genetic manipulation of cPLA2 and analyses of ATF4 and mTOR/PRC2 signaling at the protein level.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|79|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb79", "comment": "Figure S3 resolution should be improved.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Claude|1", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "The theoretical results in the supplementary proofs (Theorem 0.1) rely on sub-Gaussian distributional assumptions for the abundance data, yet the simulation studies generate data from Negative-Binomial distributions, which are heavy-tailed count distributions that do not generally satisfy sub-Gaussian conditions. This mismatch undermines the applicability of the theoretical convergence guarantees to the simulated (and subsequently, real) data.\n\n\"Suppose \\( a_{ij} - E(a_{ij})|M_{ij} = 1 \\) and \\( e_{ij} \\) follow sub-Gaussian distributions.\"\nThis assumption from Lemma 0.1 in the Supplementary Notes is fundamental to the theoretical results. Sub-Gaussian distributions have light tails with exponentially bounded moment generating functions. This assumption is used to derive concentration inequalities (via Bernstein's inequality) that underpin the convergence rates in Theorem 0.1. Without this assumption holding, the stated convergence rate of \\( O_p(\\sqrt{\\log d / n}) \\) may not apply.\n\"We generated \\( n = 50 \\) independent samples with \\( d = 100 \\) taxa, \\( n = 100 \\) independent samples with \\( d = 200 \\) taxa from Negative-Binomial distributions \\( A \\sim NB(\\mu, \\alpha) \\)\"\nThe simulation section explicitly states that data were generated from Negative-Binomial distributions. The Negative-Binomial distribution is a discrete count distribution that exhibits overdispersion and heavier tails than sub-Gaussian distributions. While log-transformation can reduce skewness, log-transformed Negative-Binomial data does not automatically satisfy sub-Gaussian properties, especially for the high-dispersion settings (\\( \\alpha = 2 \\)) used in the simulations. This creates a theoretical-empirical disconnect that the paper does not address or acknowledge.\n\"Since the square of a sub-Gaussian random variable is sub-exponential, we have \\( (\\eta_{il} + \\eta_{im})^2 - E(\\eta_{il} + \\eta_{im})^2 \\sim \\text{subE}(\\lambda) \\)\"\nThe proof of Lemma 0.1 explicitly uses the property that squares of sub-Gaussian random variables are sub-exponential to apply Bernstein's inequality. This property would not hold for Negative-Binomial data or even log-transformed Negative-Binomial data under high dispersion. The theoretical guarantees are therefore not directly applicable to the simulation setting, making it unclear whether SECOM's good empirical performance is explained by the theory or coincidental.\n\"Microbiome datasets are compositional: and this is not optional... The development of rigorous statistical methods for compositional data is an open area of research\" [[1]](#ref1)\nAs noted in the microbiome literature, count data from sequencing experiments typically follow overdispersed distributions like Negative-Binomial, not sub-Gaussian distributions. This is a well-known characteristic of microbiome data. The theoretical framework should ideally accommodate this reality rather than assume sub-Gaussian properties.\n\nReferences:\n[1] [Gloor, G. B., Macklaim, J. M., Pawlowsky-Glahn, V. & Egozcue, J. J. Microbiome datasets are compositional: and this is not optional. Front. microbiology 8, 2224 (2017).](https://www.frontiersin.org/articles/10.3389/fmicb.2017.02224/full)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Claude|2", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "The comparison between SECOM and competing methods (SparCC, proportionality, SPIEC-EASI) uses fundamentally different sparsity strategies that may disadvantage the competing methods. SparCC uses a fixed threshold of 0.3 as recommended in its original paper (which was designed for network inference, not correlation matrix estimation), while proportionality uses an ad-hoc 5th percentile cutoff, creating an uneven evaluation landscape.\n\n\"For SparCC, we used a cutoff of \\( \\rho_t = 0.3 \\) as recommended in the SparCC paper to construct a sparse correlation matrix, i.e., \\( \\hat{\\rho}_{lm} = \\hat{\\rho}_{lm} I(\\hat{\\rho}_{lm} > \\rho_t) \\)\"\nThe fixed threshold of 0.3 for SparCC is taken from the original network inference context, where the goal was to identify strong associations for network construction, not to minimize correlation matrix estimation error. Using this threshold for comparing estimation accuracy (Frobenius norm, spectral norm) puts SparCC at a disadvantage because it was never optimized for these metrics. A fair comparison would involve tuning the threshold for each method to optimize the evaluation criterion.\n\"For proportionality, to deal with the asymmetric issue, the symmetrized form \\( \\phi_{lm} = \\min(\\phi_{lm}, \\phi_{ml}) \\) was used. Since the closer \\( \\phi \\) is to zero, the stronger the proportionality, we set the 5th percentile of all \\( \\phi_{lm} \\) (denote it as \\( \\phi_5 \\)) as the cutoff value\"\nThe 5th percentile cutoff for proportionality is an ad-hoc choice that is not data-driven or optimized. This arbitrary selection disadvantages the proportionality method because the optimal threshold may vary significantly depending on the data characteristics. In contrast, SECOM uses either p-value filtering with a chosen significance level or soft-thresholding with a tuning parameter, both of which are more principled approaches.\n\"SparCC... estimates the correlations between the underlying absolute abundances using the log-ratio transformation... Under mild assumptions—that the underlying network is large and sparse—SparCC accurately recovers the correct correlation structure\" [[2]](#ref2)\nAs noted in the original SparCC paper [[2]](#ref2), SparCC was designed for inferring correlation networks under sparsity assumptions, not for minimizing matrix estimation error. The benchmark in this paper evaluates matrix estimation accuracy, which is a different objective than what SparCC was designed for. This represents a misalignment between the method's intended purpose and the evaluation criteria.\n\"We benchmark the performance of eight correlation techniques on simulated and real data... Also tested is the ability to distinguish signals from noise, and detect a range of ecological and time-series relationships\" [[3]](#ref3)\nThe benchmark study by Weiss et al. [[3]](#ref3) showed that different correlation methods have different strengths depending on the evaluation context. A fair comparison should acknowledge that methods optimized for different objectives may not perform equally well on all metrics, rather than declaring one method superior across all settings.\n\nReferences:\n[2] [Friedman, J. & Alm, E. J. Inferring correlation networks from genomic survey data. PLOS computational biology 8, e1002687 (2012).](https://journals.plos.org/ploscompbiol/article?id=10.1371/journal.pcbi.1002687)\n[3] [Weiss, S. et al. Correlation detection strategies in microbial data sets vary widely in sensitivity and precision. ISME J 10, 1669–1681 (2016).](https://www.nature.com/articles/ismej2015235)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Claude|3", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "The real data analysis of the NoMIC infant gut microbiome data uses very small sample sizes (46, 44, and 34 samples at days 30, 120, and 365 respectively), yet the paper presents correlation estimates as point estimates without confidence intervals or other uncertainty measures. This limits the reliability of the biological conclusions drawn about temporal patterns of microbial correlations.\n\n\"We chose to study the correlations at 30, 120, and 365 days, with 46, 44, and 34 sequenced samples, respectively\"\nWith only 34 samples at day 365, estimating correlations among the top 10 bacterial families (potentially 45 pairwise correlations) involves a high-dimensional estimation problem where the number of parameters is comparable to the sample size. Standard correlation estimates become highly variable in this regime, yet the paper does not report standard errors, confidence intervals, or bootstrap estimates for the reported correlations. This omission makes it difficult to assess whether observed differences in correlations are statistically meaningful.\n\"Results demonstrated that SECOM methods, namely, SECOM(Thresholding) and SECOM(Filtering) were the only methods successfully quantified microbial correlations between ecosystems.\"\nWhile the simulation results support SECOM's performance, the real data analysis lacks the uncertainty quantification needed to support claims about discovering temporal patterns. For instance, the paper reports correlations like \"SECOM (Pearson2) = -0.45\" without indicating whether this estimate is statistically distinguishable from zero or from other time-point estimates given the small sample size. The claim of characterizing \"temporal changes in correlations\" would be strengthened by formal testing of whether correlations differ significantly across time points.\n\"Furthermore, as can be seen from the p-value distribution provided in Supplementary Fig. 1b, unlike the existing methods, SECOM does not suffer from inflated false correlations between taxa.\"\nWhile the p-value calibration in simulations is encouraging, the paper does not show p-values for the real data correlations. In the NoMIC analysis, many correlations are reported as nonzero, but without p-values or confidence intervals, readers cannot assess which are statistically significant. Given the small sample sizes and multiple comparisons (many pairwise correlations), false discovery rate correction would also be appropriate but is not mentioned for the real data analysis.\n\"For a study that aims to achieve a target correlation with a high level of precision such as fixing its 95% confidence level width at 0.1, the recommended sample size requirement is between 62 (for r = 0.9) to 1274 (for r = 0.3) for Pearson's correlation\" [[4]](#ref4)\nSample size guidelines for correlation estimation suggest that achieving narrow confidence intervals (width 0.1) for moderate correlations (r = 0.3) requires over 1,000 samples [[4]](#ref4). The NoMIC analysis uses only 34-46 samples, suggesting that the correlation estimates may have wide confidence intervals that could span from weak negative to weak positive correlations, undermining conclusions about specific relationships.\n\nReferences:\n[4] [Bujang, M. A. & Baharum, N. An elaboration on sample size determination for correlations based on different computational estimation approaches. BMC Med Res Methodol 24, 114 (2024).](https://pmc.ncbi.nlm.nih.gov/articles/PMC11148401/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Claude|5", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "The simulation study for evaluating nonlinear correlation detection uses only quadratic (polynomial degree 2) relationships. This limited scope does not demonstrate SECOM's ability to detect other forms of nonlinearity that may be relevant in ecological contexts, such as threshold effects, saturation curves, or more complex interaction patterns.\n\n\"For the first 50 taxa, each taxon was set to be quadratically correlated with its adjacent taxon. Specifically, \\( a_{ij} \\) is orthogonal polynomials of degree 2 to \\( a_{i-1,j} \\) for \\( i \\in \\{1, \\ldots, 50\\} \\)\"\nThe nonlinear simulation exclusively uses quadratic relationships (orthogonal polynomials of degree 2). While quadratic relationships are a natural starting point, they represent only one type of nonlinearity. Ecological systems often exhibit threshold effects, sigmoidal relationships (e.g., predator-prey dynamics), exponential relationships (e.g., growth models), or more complex multimodal patterns. The simulation study does not evaluate SECOM's performance under these alternative nonlinear scenarios, limiting the generalizability of the conclusions.\n\"Due to complex underlying interactions, some microbes may correlate nonlinearly. Yet, there are no measures in the literature that quantify these nonlinear relationships.\"\nThe paper motivates the need for nonlinear correlation methods by citing complex underlying interactions in microbiomes. However, the simulation only tests one specific type of nonlinearity (quadratic), which may not be representative of the \"complex underlying interactions\" mentioned. Real ecological interactions could involve step functions, periodic relationships, or multivariate interactions that quadratic polynomials cannot capture. Demonstrating SECOM's performance under diverse nonlinear scenarios would strengthen the claim that it can detect complex interactions.\n\"Considering the possibility of the nonlinear association among microbial species, the non-parametric Kendall's rank correlation based on rank instead of value is another candidate. The third correlation method is the recently developed maximal information coefficient (MIC) method which measures how much information two random variables share. This correlation method is claimed to be able to capture both linear and nonlinear associations\" [[6]](#ref6)\nOther methods in the literature for detecting nonlinear associations, such as MIC [[6]](#ref6), have been evaluated on diverse nonlinear relationships including sinusoidal, exponential, and other complex patterns. The SECOM evaluation is narrower in scope, making it difficult to compare SECOM's detection power with alternatives across the full range of potential nonlinearities.\n\nReferences:\n[6] [Chen, L. et al. A Multivariate Distance-based Analytic Framework for Microbial Interdependence Association Test in Longitudinal Study. Genet Epidemiol 41, 769-778 (2017).](https://pmc.ncbi.nlm.nih.gov/articles/PMC5696116/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|GPT|1", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "This paper makes an inaccurate novelty claim and then draws an unsupported conclusion that existing microbiome association methods cannot identify nonlinear relationships (Validity; Conclusions; Originality and significance), specifically in the Abstract and the nonlinear-simulation comparison.\n\n“Due to complex underlying interactions, some microbes may correlate nonlinearly. Yet, there are no measures in the literature that quantify these nonlinear relationships.”\nThis statement is a strong, field-wide novelty claim (“no measures in the literature”), but the paper itself later relies on distance correlation, which is an established dependence measure rather than a new concept. More importantly, the broader microbiome-network literature already used non-linear dependence measures (e.g., mutual information, distance-based similarities) prior to this preprint, so the novelty framing is factually incorrect. Because novelty is part of the paper’s motivation, this overstatement directly affects how readers interpret both significance and contribution. The paper does not qualify the claim as “no measures that handle compositionality, bias, and nonlinear dependence simultaneously,” which would be narrower and potentially defensible. As written, the claim is contradicted by readily-citable existing tools and methods used in microbiome association inference. This undermines the credibility of the paper’s framing and the strength of its “first in the literature” assertions.\n“Since, with the exception of SECOM, none of the existing methods are designed to measure nonlinear relationships, we only compared these methods in their ability to recover sparsity.”\nThis passage explicitly limits the comparison set to methods “not designed to measure nonlinear relationships,” and then proceeds to use the resulting outcomes to argue that SECOM has a unique advantage for nonlinear dependence. That inference is not logically supported because the experiment excludes well-known nonlinear dependence measures and nonlinear network-inference approaches that could serve as proper baselines. The evaluation design therefore cannot justify a conclusion about the broader state of the art, only about the subset of baselines chosen. In other words, the comparison is constructed so that competitors are expected to fail on nonlinear dependence by design. Because the conclusion is used to argue superiority for nonlinear relationships, it affects the paper’s main empirical claims. A fair test would include at least one established nonlinear association measure (e.g., mutual information) and/or a tool that implements such measures for microbial count/abundance tables.\n“As expected, none of the competing methods identify nonlinear relationship (Fig. 3).”\nThis sentence states a general conclusion about the competing methods’ ability to identify nonlinear relationships, but it is not supported by the experimental design described in the paper. The authors explicitly chose methods that are “not designed” for nonlinear dependence, which makes it unsurprising that they perform poorly in this setting. More critically, the conclusion does not account for existing microbiome association approaches that do support nonlinear dependence measures, so it cannot be read as a statement about the literature at large. Even within the chosen baselines, the statement “none identify” conflates “not targeted for nonlinear dependence” with “incapable,” which is a stronger claim than the evidence warrants. Because this claim is presented as an “expected” generalization, it risks misleading readers about what the simulation actually establishes. The paper should narrow the claim to the specific methods evaluated or expand the baseline set to include nonlinear-capable alternatives.\n“In the next step, the user can select from a number of different correlations (Pearson, Spearman, Kendall), similarities (mutual information, Steinhaus, distance correlation etc.) or dissimilarities (Kullback Leibler, Euclidean, Bray Curtis, Jensen-Shannon etc.) to score the association strength between the objects.” [[1]](#ref1)\nThis sentence directly contradicts the paper’s Abstract claim that “there are no measures in the literature” for nonlinear relationships, because it documents an existing microbiome-focused network tool that supports mutual information and distance correlation among its association measures. The quote also shows that distance correlation is not a newly introduced dependence concept in this domain; it was already operationalized in software used for microbial community data. The existence of such tools does not invalidate SECOM’s approach, but it does invalidate the categorical novelty framing and weakens claims of being first. In addition, it implies that the nonlinear simulation comparison in the preprint is incomplete, because methods that are explicitly capable of nonlinear dependence could have been included. This matters for the validity of the empirical “only SECOM” conclusion. The paper should either revise the novelty claim or expand comparisons to include such nonlinear-capable baselines.\n“Better able to detect non-linear dependencies than other measures.” [[1]](#ref1)\nThis statement from a microbiome-networking tool paper explicitly characterizes mutual information as a method for detecting non-linear dependencies, contradicting the preprint’s claim that the literature lacks such measures. It also highlights a common practice: when nonlinear dependencies are plausible, researchers often evaluate association measures beyond linear correlation. By not comparing against at least one non-linear dependency measure, the preprint’s nonlinear evaluation cannot substantiate the breadth of its claimed advantage. The contradiction is not merely semantic; it impacts the interpretation of the paper’s central contribution and benchmarking. If mutual information (and other measures) are known to detect non-linear dependencies, the paper’s conclusion that other methods “identify nonlinear relationship” at ~0 TPR is not generalizable. This directly affects the reliability of the paper’s conclusions about nonlinear association discovery.\n\nReferences:\n[1] Faust, K. & Raes, J. *CoNet app: inference of biological association networks using Cytoscape* (F1000Research, 2016). [https://pmc.ncbi.nlm.nih.gov/articles/PMC5089131/](https://pmc.ncbi.nlm.nih.gov/articles/PMC5089131/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "The method relies on the assumption that the noise variance is much smaller than the signal variance, which is unrealistic for microbiome data known to be noisy and overdispersed.\n\n\"Assumption 0.2 (Small noise-to-signal ratio). \\[ \\sigma_e^2 \\ll \\sigma_{ll}^0. \\]\"\nThis assumption is critical for the proposed estimator to be consistent. However, microbiome data is characterized by high levels of noise, including technical noise (e.g., PCR amplification bias, sequencing errors) and biological variation that is not captured by the model [3]. The assumption that this noise is negligible compared to the signal variance ($\\sigma_{ll}^0$) is likely violated in many real-world scenarios.\n\"Then we have: \\[ \\rho_{lm} = \\frac{\\sigma_{lm}}{\\sqrt{\\sigma_{ll} \\sigma_{mm}}} = \\frac{\\sigma_{lm}^0}{\\sqrt{(\\sigma_{ll}^0 + \\sigma_e^2)(\\sigma_{mm}^0 + \\sigma_e^2)}} \\approx \\frac{\\sigma_{lm}^0}{\\sqrt{\\sigma_{ll}^0 \\sigma_{mm}^0}} = \\rho_{lm}^0 \\]\"\nThe derivation shows that if the noise variance $\\sigma_e^2$ is not negligible, the estimated correlation $\\rho_{lm}$ will be attenuated (biased towards zero) compared to the true correlation $\\rho_{lm}^0$. Given the high noise levels in microbiome data, this attenuation bias could be substantial, leading to false negatives and underestimation of correlation strength. The paper does not provide a robustness analysis or a correction for this bias when the assumption is violated.\n\"Waste Not, Want Not: Why Rarefying Microbiome Data Is Inadmissible\" [3]\nMcMurdie and Holmes (2014) discuss the overdispersion and noise inherent in microbiome data, emphasizing that simple models often fail to capture the complexity of the data. The \"small noise\" assumption in SECOM simplifies this complexity in a way that may not be justifiable.\n\nReferences:\n[3] McMurdie, P. J., & Holmes, S. (2014). Waste Not, Want Not: Why Rarefying Microbiome Data Is Inadmissible. PLOS Computational Biology, 10(4), e1003531. https://doi.org/10.1371/journal.pcbi.1003531", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "The paper fails to provide a clear and reproducible description of how the variances used in the weighted average estimator are estimated.\n\n\"Taking into account the variance of residuals \\( o_{ij} - \\bar{o}_j \\), a weighted average is proposed as follows: \\[ \\textcircled{1} = \\bar{s}_i - \\bar{s}_. = \\sum_{j \\in d(i)} w_j (o_{ij} - \\bar{o}_j), \\] where \\( w_j = \\frac{1}{Var(o_{ij} - \\bar{o}_j)} / \\sum_{l \\in d(i)} \\frac{1}{Var(o_{lj} - \\bar{o}_l)} \\).\"\nThe term $Var(o_{ij} - \\bar{o}_j)$ represents the variance of the observed log-abundance residuals. However, the paper does not specify how this variance is estimated from the data. If the sample variance of $o_{ij} - \\bar{o}_j$ is used, it would be circular because $o_{ij}$ contains the bias term $s_i$ that the method aims to estimate. Without a clear definition of how these weights are calculated, the method is not reproducible.\n\"The statistical details are provided in the Methods section of the paper.\"\nDespite this claim, the critical detail of variance estimation for the weights is missing from the Methods section. This omission prevents independent implementation and verification of the method.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "The model allows for the sampling faction and sampling efficiency to differ between samples and taxa (S_i and C_j in the model), which is very appealing. These can be considered bias factors which act multiplicatively on the read counts. However, it seems that these factor only apply to the non-zero element in the count table. In other words, if a taxon has zero read count, the model assumes the zero count is accurate and S_i and C_j do not impact them. This is a limitation. You can easily imagine a situation that a taxon is in fact present in the sample, but if sequenced with low sampling efficiency, we observe zero read count for this taxon, yet if sequenced with high sampling efficiency, we observe non-zero read count. This can be problematic especially when more than 90% of the reads can be zeros. Could the authors elaborate this point, and/or assess the sensitivity of the proposed model against violations of such a simplification?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "The authors provided two approaches for selecting important linear correlations, either through the “Thresholding” or “filtering” approach. However, it is not clear how the hypothesis testing (for calculating the p-values) is conducted, and how the “thresholding” is conducted.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "How sensitive is the method to the choice of pseudo-counts, as the log transformation was applied to read counts?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "Is there a theoretical guarantee of FDR of the proposed method on the identified correlations?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "The proposed method models the read counts instead of proportions with S_i and C_j to capture the efficiency of sequencing at the sample and taxon level. Is the model consistent with a compositional model, i.e., a model that works on relative abundances, and only has one set of vectors C_j to capture the efficiency in sequencing each taxon?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "The extension of the model in handling multiple ecosystems is not very clearly described.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "supplemental figure 2 doesn’t seem to make sense. Are both X and Y-axis log-transformed relative abundances? The number of samples are smaller than what was described in the paper. Further, there seems to have over-fitting for the LOESS curve: there was no point between 0.5 and 1, and how could the loess curve have a peak around x = 1.5?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "There are mathematical assumptions behind the method and the theorems underlying it. It would be helpful if the readers can get some intuitive interpretation of these assumptions?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "I was confused for quite a while about how the settings in the paper translate to the context of a human microbiome study -- what is an “ecosystem” in a human microbiome study: a sample? a group of samples, perhaps defined by some phenotype or disease? Are analyses within an ecosystem just analyses of samples who all belong to the same group?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "It would be helpful to provide some more explicit examples early in the paper and translate them into the language you use for the rest of the paper to clarify this for readers.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "When you discuss comparison methods, one of the critiques is that introduction of sparsity is done in a relatively arbitrary/ad hoc way. But isn’t a cutoff of, say, 0.3 in SPARCC conceptually similar to your filtering method, where you choose a cutoff of alpha and set values below that to zero (although SPARCC’s version is based on correlation value rather than P-value)? You also apply the Filtering approach directly to the proportionality statistic (and P-value filtering is not entirely a new idea). I’m not sure whether this is as strong a differentiator between your method and previous methods as is implied (although you do see some improvement over SPARCC’s method).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "Relatedly, is your statement that SPARCC recommends a cutoff of 0.3 based on the sentence from their manuscript “For clarity, only edges corresponding to correlations whose magnitude is greater than 0.3 are drawn.”? They also adapt the correlation estimation method to “reinforce sparsity” (their phrasing) – for accuracy, might be worth briefly mentioning that it’s not a standard correlation estimate when you describe their method on page 7.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "In the Discussion, it is pretty well established by now that Pearson and Spearmon correlation coefficients don’t work with microbiome data. In my opinion, the more interesting comparators for your method are SparCC and SPIEC-EASI, which were designed to handle microbiome data challenges and have ways to introduce sparsity. I’d prefer to see the takeaways related to these methods highlighted in the Discussion. If I understand your results correctly, the argument you’d make in that case is:\n\n- SECOM is better at recovering sparsity patterns than SparCC\n\n- Although SECOM and SPIEC-EASI perform similarly for TPR, FPR etc. in the case of linear associations, SPIEC-EASI is more computationally intensive – and it’s not great at sparsity recovery with nonlinear associations.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "True correlation among 50 out of 100 taxa does not seem particularly sparse to me. (Maybe your equation on page 2 is not accurately representing your sparsity pattern? That equation suggests taxon 1 is correlated with 2, 3, 4, ..., 50, and similarly for all other taxa in the first 50. The text would make me think taxon 1 was correlated with taxon 2, 2 with 1 and 3, 3 with 2 and 4, and so on.) SparCC says its sparsity assumption is strongly violated if >30% of pairs are correlated. If it’s really the case that the first 50 taxa are all associated, it might be worth doing some simulations with higher levels of sparsity.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "You examine how well the linear and nonlinear correlation coefficients identify whether two taxa are correlated [in that way]. Have you examined how well they together identify whether the association is linear or nonlinear? You comment on what you expect to see in Remark 3 (Methods section), and in your real data application, you make conclusions about it based on the pair of correlation coefficients – I’d be curious to see this in simulation results, too. That is, if you look at the pair (Pearson cor, Distance cor) how often do you see (0, 0), (0, nonzero), (nonzero, 0), and (nonzero, nonzero) in each sim setting?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "Can you comment on how realistic the assumptions are? (The signal to noise assumption particularly caught my eye.)", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "Figure 1 might be easier for readers to scan quickly if the grid for 1c-e matched up with 1a-b (i.e., (T1,T1) in the upper right corner).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Human_2|10", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "Supplementary Figure 2 – are the black points the observed data? If so, doesn’t it seem like the LOESS line is a bit overfit? I don’t see any reason it should swing up to a value of 5 for Ruminococcaceae with no observed values anywhere near that high. I agree that there are probably situations with nonlinear associations between two taxa – this just seems like it might not be one of those, or at least not to the degree that the LOESS curve would suggest.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Human_2|11", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "Page 2, third from last paragraph – you state that the methods are not scale invariant when computing correlation across two or more ecosystems. Can you put this in context with an example?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Human_2|13", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "Supplementary Figure 5 – you use distance correlation for the whole figure (not linear/Pearson correlation), so it seems that the legend should read something like “... for (a) linear form of association, (b) quadratic form of association”.", "reviewer_type": "human", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|80|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "SECOM is not packaged as a tool for widespread use. The code is available in R, but it is not a package that can be easily install (for example, using bioconductor or galaxy or bioconda).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "This section on the Norwegian infant data is purely descriptive. Particularly if the authors were to add a comparison to existing methods (see #2), then it would not be a strong argument that their method is superior.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "The authors routinely use the term \"linear\" where they should have written \"monotonical\", leading to several incorrect statements, including unfairly disparaging other methods. For example: \"Pearson and Spearman correlation coefficients are measures of linear associations and may not be suitable to describe nonlinear relationships.\" This is wrong. Spearman is very much a measure of non-linear relationships. It fails in the parabolic example ( [x-5]^2 ) the authors give because that is a non-monotonic relationship.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "The authors claim that \"as demonstrated in this paper, relationships between a pair of microbes is not always linear as there exist complex interactions among them.\" While I believe the statement is true (and widely accepted), this paper does not demonstrate this at all! If one interprets the statement as discussing non-monotonicity (see #4 above), however, then it is not clear to me that this is as widely accepted in the field.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|80|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb80", "comment": "The multiple ecosystems setting could be better motivated. It is only presented for a simulated setting and it is not clear what this setting is emulating. If I understand correctly, the authors are considering for example samples from the gut and skin of the sample individuals. In particular, it seems to be different from what is provided by FlashWeave (https://doi.org/10.1016/j.cels.2019.08.002 — a method not considered by the authors), which also provides the ability to work across ecosystems.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Claude|1", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "The single-cell impedance sensing experiment demonstrating the 20.2 dB gain is based on data from only one T98G cell adhered to a single device, with error bars derived from temporal replicates rather than independent biological replicates, which severely limits the statistical validity and generalizability of the findings.\n\n\"An optical image of the final experimental configuration is reported in Figure 3a, showing a single T98G cell positioned at the center of the PEDOT:PSS channel.\"\nThis statement confirms that the entire single-cell detection experiment is based on a single cell. In cell biology research, particularly for claims about sensor performance, biological variability between cells is substantial and necessitates multiple independent measurements from different cells. A single cell cannot represent the population-level behavior, and the observed 20.2 dB gain may not be reproducible with other cells of the same type.\n\"To provide a direct comparison between the sensing performances, we averaged the current amplitudes acquired when the cell is detached (t<30 min and t=240 min) and attached (120<t<180 min), and we subtracted the resulting values to calculate the experimental sensitivity for both devices.\"\nThe averaging described here is across different time points of the same cell on the same device, not across multiple independent cells or devices. This approach captures measurement noise but not biological variability, which is the dominant source of uncertainty in cell-based biosensing experiments.\n\n* Quote (from Figure 3 caption): \"Error bars are obtained by averaging between n=4 measurements acquired at different time.\"\nThe n=4 measurements are temporal replicates of the same cell attachment event, not independent biological replicates. This methodology conflates technical replicates with biological replicates, leading to artificially narrow error bars that do not reflect the true uncertainty in single-cell detection performance.\n\"Furthermore, in experiments involving cells, increasing the number of devices is crucial. Probing the behavior of the cells on a single micrometric spot might lead to over- or under-estimation of the system behavior due to the low statistical relevancy of sampling a surface containing a few tens of cells, compared to the several thousand present in the whole cell culture.\" [[1]](#ref1)\nThis recent publication in Nature Communications explicitly states the importance of multiple devices and statistical relevance in cell-based OECT experiments. The paper under review contradicts this established principle by basing its key findings on a single cell measurement, which the literature identifies as potentially leading to over- or under-estimation of performance.\n\nReferences:\n[1] Decataldo, F., et al. \"Reconfiguration of organic electrochemical transistors for high-fidelity sensing.\" *Nature Communications* **15**, 5827 (2024). https://www.nature.com/articles/s41467-024-50792-1", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Claude|2", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "The paper uses a 50 µm dielectric microparticle to simulate single-cell sensing, but this model has significant size mismatch with the actual T98G cells used later, and lacks the biological complexity (membrane capacitance, dynamic cell-substrate adhesion, focal adhesion formation) that critically influences impedance measurements of living cells.\n\n\"The setup contains a dielectric microparticle (with diameter of 50 µm) attached to the bottom part of an AFM cantilever to have micrometric control of its position in the 3 spatial directions.\"\nThe 50 µm microparticle is substantially larger than typical mammalian cells. T98G glioblastoma cells typically have diameters of approximately 15-35 µm depending on culture conditions and adhesion state. The size mismatch means the impedance changes measured with the microparticle may not accurately reflect the magnitude or spatial characteristics of changes induced by real cells.\n\"Qualitatively, this response is expected, as the microsphere represents a barrier for the ionic current in the electrolyte: when it is close to the sensor surface, the half space through which ions can approach the active layer is reduced, thus increasing the effective impedance of the electrolyte Zel.\"\nThis purely physical explanation treats the cell as a passive dielectric barrier, ignoring the complex biological properties that cells bring to impedance sensing. Living cells form focal adhesions with specific spacing, have dynamic membrane properties, and create cell-substrate gaps with electrochemically active interfaces. The paper does not discuss or validate how well the simplified microparticle model captures these biologically relevant impedance contributions.\n\"We note that in first order approximation a similar response is expected when a biological cell adheres to the sensor surface.\"\nThe claim of similarity is stated without validation. The paper does not provide any experimental correlation or theoretical analysis comparing the microparticle response to actual cell responses. Standard practice in biosensor modeling requires validation that surrogate models accurately represent the target analyte's behavior across relevant operating conditions.\n\"Impedance spectra of the OECTs changed drastically when HEK 293 cells were adhered to the OECT gates. To confirm the single-cell sensitivity, individual cells were removed from the device surface with patch-clamp pipettes while impedance measurements were performed.\" [[2]](#ref2)\nThe Hempel et al. study cited by the authors used actual cell manipulation (removal via patch-clamp pipettes) to validate single-cell sensitivity, rather than surrogate microparticle models. This demonstrates that direct cell-based validation is feasible and represents the established methodology for verifying single-cell detection capabilities.\n\nReferences:\n[2] Hempel, F., et al. \"PEDOT:PSS organic electrochemical transistors for electrical cell-substrate impedance sensing down to single cells.\" *Biosensors and Bioelectronics* **180**, 113101 (2021). https://pubmed.ncbi.nlm.nih.gov/33691239/", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Claude|3", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "The mathematical model uses a parameter fOECT that is individually adjusted for each sensor to optimize the fit, rather than being derived from physical principles or held constant, which introduces arbitrary flexibility that could mask model inadequacies.\n\n\"The factor fOECT in eqn. 1 determines how the gate current is distributed between the source and the drain terminal and is typically assumed to be equal to 0.5.\"\nThe paper acknowledges that fOECT is typically assumed to be 0.5 based on symmetric current distribution between source and drain terminals. This standard assumption provides a physically grounded constraint that enables fair comparison across devices and with other published work.\n\"For this reason, fOECT was not assumed as constant in this experiment, but its value was set for each sensor in order to best fit the experimental data with the model.\"\nBy allowing fOECT to vary freely for each sensor, the model gains an additional degree of freedom that can compensate for other model inaccuracies or device-to-device variations that should ideally be captured by the physical parameters. This fitting approach makes it difficult to assess whether the model correctly captures the underlying physics or simply fits the data through parameter adjustment. The paper does not report the range of fOECT values obtained, nor does it analyze what physical factors might cause the variation.\n\"While Bernard's model marks the first attempt to predict OECTs' transient response, the simplifications introduced in the model limit its accuracy... Other models have improved Bernard's model and given a physical interpretation to the factor f.\" [[3]](#ref3)\nRecent literature has established physical interpretations for the f factor in OECT models, enabling principled determination of this parameter rather than arbitrary fitting. The paper under review could have adopted these improved models to provide a more rigorous analysis without relying on free parameter adjustment for each device.\n\nReferences:\n[3] Cucchi, M., et al. \"A guide for the characterization of organic electrochemical transistors and channel materials.\" *Chemical Society Reviews* **52**, 5012 (2023). https://pubs.rsc.org/en/content/articlehtml/2023/cs/d2cs00920j", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Claude|4", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "The paper focuses its cell sensing analysis primarily at a single frequency (625 Hz, the OECT cutoff frequency), whereas established Electric Cell-substrate Impedance Sensing (ECIS) methodology emphasizes that multi-frequency measurements are essential for comprehensive characterization of cell-substrate interactions.\n\n\"The sensing frequency was selected in correspondence to the OECT cutoff (measured at time t=0), where the model indicates the maximum sensitivity.\"\nWhile selecting the frequency of maximum sensitivity is reasonable for demonstrating device performance, cell biology applications require multi-frequency analysis to differentiate between paracellular barrier resistance, cell-substrate adhesion, and membrane capacitance. The paper's focus on a single frequency optimized for OECT gain may not correspond to the optimal frequency for extracting biologically meaningful cell parameters.\n\"The OECT gain is highest in the low-frequency regime, but is still significant in the 0.1-10 kHz range, where the impedance of the cell layers is typically measured.\"\nThe paper acknowledges that cell impedance is typically measured across a frequency range (0.1-10 kHz), yet the single-cell experiments focus primarily on demonstrating gain at 625 Hz. A more comprehensive analysis would characterize how the OECT gain affects the extraction of different cell parameters across the relevant frequency spectrum.\n\"ECIS is the only impedance biosensor to use multifrequency AC. This is a major distinguishing factor in comparison to xCELLigence technology from ACEA, which generates the data from a single AC frequency... impedance measured across multiple frequencies can be mathematically modeled using the ECIS software to derive several important parameters which collectively relate to the overall barrier formation of the cells. These are Rb (resistance of the paracellular space), α (resistance due to basal adhesion), and Cm (capacitance of the cell membrane).\" [[4]](#ref4)\nThe established ECIS literature explicitly identifies multi-frequency analysis as essential for extracting distinct cell parameters (paracellular resistance, basal adhesion, membrane capacitance). The paper's single-frequency approach limits the biological information that can be extracted from the impedance measurements, even if the OECT provides gain at that frequency. The paper does not discuss how the frequency-dependent OECT gain would affect the extraction of these biologically important parameters.\n\nReferences:\n[4] Benson, K., et al. \"The Importance of Multifrequency Impedance Sensing of Endothelial Barrier Properties.\" *Tissue Barriers* **1**, e25733 (2013). https://pmc.ncbi.nlm.nih.gov/articles/PMC6163417/", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|GPT|1", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "The paper’s quantitative model for OECT impedance-sensor gain is not independently parameterized because it introduces a device-specific fitted gate-current partition factor, which undermines the validity of claims that the model “correctly predicts” sensitivity/gain trends and yields general optimization guidelines.\n\n“Possible contributions due to parasitic capacitances are neglected for simplicity. The factor fOECT in eqn. 1 determines how the gate current is distributed between the source and the drain terminal and is typically assumed to be equal to 0.5. Several studies demonstrate that the fOECT factor is slightly dependent on VD,DC, and VG,DC as well as on channel geometry. For this reason, fOECT was not assumed as constant in this experiment, but its value was set for each sensor in order to best fit the experimental data with the model.”\nThis passage states that a key factor controlling the measured source current is not measured, but instead tuned “for each sensor” to match the data. That makes the agreement between model and measurements partly tautological, because the model can absorb discrepancies by adjusting fOECT. A model that is presented as “quantitative” and used for design guidelines should, at minimum, specify how all parameters are obtained independently (or provide uncertainty propagation showing robustness to plausible fOECT variation). Here, the fitting choice can inflate perceived predictive accuracy across geometries and conditions, since fOECT is allowed to vary in exactly those dimensions. The problem is not that fitting is used at all, but that the fitted parameter is central to the gain computation and is not constrained by a separate experiment. As a result, conclusions about “clear guidelines for optimization” are less reliable than the text implies.\n“The model correctly predicts the dependence of the sensitivity on frequency, sensor geometry and semiconductor materials properties such as carrier mobility and volumetric capacitance.”\nThis sentence is a strong predictive claim, yet the model’s agreement is explicitly supported by per-device tuning of fOECT and by other fit-derived quantities (e.g., extracted Zel and Cch). When a model is calibrated to each device, “correctly predicts” should be replaced by a more limited claim such as “fits” or “describes” the observed data. Without an out-of-sample validation (e.g., fixing fOECT from one bias/geometry and predicting another), it is unclear which aspects are genuinely predicted versus accommodated by calibration. This matters because the paper uses the model to justify geometry choices and to interpret the gain mechanism. In the biosensor optimization context, practitioners need to know whether the model generalizes to new devices without refitting. The paper does not provide that kind of generalization test in the main text.\n“In this work, we combine OECT-based drain current measurements with simultaneous measurement of more traditional impedance sensing using the gate current to produce complex impedance traces, which show low error at both low and high frequencies.” [[2]](#ref2)\nThis prior work highlights a common practice for impedance sensing with OECTs: measuring gate current explicitly rather than inferring its contribution via an assumed (or fitted) partition factor. The paper under review instead folds the gate-current contribution into a parameter (fOECT) that is optimized to match data, which can mask systematic errors in the current decomposition. The contrast is important because the decomposition of measured current into channel and gate components is central to the claimed “amplification” mechanism. If direct measurement of gate current is feasible (as shown here), then leaving it unmeasured makes the gain attribution less secure. The evidence does not imply the reviewed model is always wrong, but it shows that a more direct experimental route exists to avoid the need for device-specific fitting of current partition. This weakens the paper’s claim to have established a rigorous quantitative framework.\n\nReferences:\n[2] [Rivnay et al., “Organic electrochemical transistors for cell-based impedance sensing” (Appl. Phys. Lett. 106, 043301 (2015) abstract via ADS)](https://ui.adsabs.harvard.edu/abs/2015ApPhL.106d3301R/abstract)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|GPT|2", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "The paper’s central methodological surrogate—replacing a biological cell with a dielectric microparticle to “simulate” single-cell impedance sensing—does not adequately capture cell-specific impedance mechanisms (membrane capacitance and paracellular pathways), so conclusions drawn from the AFM microparticle experiment may not transfer to real cell adhesion/detachment sensing.\n\n“As cellular in-vitro experiments are inherently difficult to control we substitute the cell by a dielectric microparticle of similar dimensions.”\nThe paper frames the microparticle substitution as a core step to obtain “highly reproducible” quantitative insight. However, similarity in size is not sufficient to reproduce the electrical boundary conditions of an adherent cell, which is not merely a dielectric obstacle in an electrolyte. Cells introduce frequency-dependent pathways through membrane capacitance and junctional/paracellular resistances, and these are often the quantities of interest in impedance sensing. A rigid dielectric bead primarily perturbs access resistance and geometric current crowding near the electrode/channel, which is only one component of cellular impedance changes. If the surrogate does not reproduce the dominant impedance elements across the studied frequency band, then geometry-optimization conclusions risk being specific to bead-blocking rather than cell-electrode coupling. The later in-vitro experiment helps, but it does not fully validate that the AFM-derived optimization generalizes across cell types and conditions.\n“We note that in first order approximation a similar response is expected when a biological cell adheres to the sensor surface.”\nThis sentence asserts similarity but does not provide an electrical argument or a control experiment demonstrating equivalence of the impedance perturbation between bead approach and cell adhesion. In impedance-based cell assays, the “response” is typically frequency dependent and arises from multiple paths, not only from reduced ionic half-space above the electrode. Calling the similarity a “first order approximation” is also ambiguous: the paper uses this approximation as the foundation for a quantitative optimization model, so it needs to be shown that neglected terms are small over the relevant frequencies. Without that, it is plausible that the surrogate overweights electrolyte-access effects and underweights membrane-related effects that dominate at higher frequencies. This matters because the paper’s claimed gain is frequency-dependent and tied to a cutoff frequency interpretation. The evidence therefore supports a concern that the surrogate may be an incomplete proxy for the biology-driven impedance spectrum.\n“When a monolayer of cells forms on the ECIS® electrode-substrate, current can flow in two different paths: 1. Through the culture medium surrounding the cells: 2. Capacitively coupling through the cell membranes: … At relatively low frequencies, the reactance is high, and there is little capacitive flow of current… Alternatively, the membrane reactance is low at high frequencies, and most of the current now passes capacitively through the plasma membranes.” [[5]](#ref5)\nThis description (from a widely used impedance-sensing methodology) makes explicit that cell impedance involves at least two distinct pathways with different frequency dependence, including capacitive coupling through membranes. A dielectric bead cannot emulate a living cell membrane’s capacitive behavior and the associated frequency-dependent shift in current pathways. Therefore, a bead-based perturbation can match some low-frequency resistive effects yet fail to reproduce the high-frequency capacitive regime that is commonly used to decouple coverage vs junctional maturation. The reviewed paper studies gains across decades of frequency and links optimization to a geometry-dependent cutoff, so missing the membrane pathway is a major limitation for transferability. Importantly, this is not a minor modeling preference; it affects which physical impedance elements are being amplified by the transistor. The surrogate thus risks guiding optimization toward amplifying the “wrong” impedance component for actual single-cell adhesion biology.\n“We apply this technique in vitro to a model epithelial tissue layer and show that the data can be fit to an equivalent circuit model yielding trans-epithelial resistance and cell layer capacitance values in agreement with literature.” [[2]](#ref2)\nThis statement underscores that real cell-layer impedance sensing typically aims to extract both resistive and capacitive elements attributable to the cell layer. That framing contrasts with the reviewed paper’s surrogate, which is defined mainly as a controlled change in electrolyte impedance Zel via bead distance. If the experimental perturbation in the surrogate does not reproduce changes in cell-layer capacitance, it is not measuring the same physical quantities that equivalent-circuit fits target in cell assays. Because the reviewed paper’s model is built around how changes in Zel map to current sensitivity, it may not capture how cell-layer elements (resistance/capacitance) alter the transfer function. This matters especially when the paper claims to provide general guidelines for “single cell sensors,” where cell-specific elements dominate. The evidence therefore supports the criticism that the surrogate is incomplete relative to established cell-impedance practice.\n\nReferences:\n[2] [Rivnay et al., “Organic electrochemical transistors for cell-based impedance sensing” (Appl. Phys. Lett. 106, 043301 (2015) abstract via ADS)](https://ui.adsabs.harvard.edu/abs/2015ApPhL.106d3301R/abstract)\n[5] [Applied BioPhysics, “Electric Cell-substrate Impedance Sensing: A Label-free Method to Continuously Monitor Cell Behaviors In Vitro” (application note PDF)](https://www.biophysics.com/public/pdf/ElectricCellsubstrateImpedanceSensingALabelfreeMethodtoContinuouslyMonitorCellBehaviorsInVitro101723.pdf)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|GPT|3", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "The paper’s headline single-cell gain result (20.2 ± 0.9 dB) is not robustly supported because the uncertainty is derived from repeated measurements over time rather than independent biological replicates (different cells/devices), limiting the reliability of the conclusions about performance and reproducibility.\n\n“However, in the OECT the single cell adhesion transient is measured with a current signal gain of (20.2±0.9) dB at 625 Hz, in close agreement with the model prediction.”\nThis sentence elevates a single-cell experiment into a quantitative performance claim with a stated uncertainty, implying a statistically meaningful measurement. Yet the manuscript does not clearly establish that the quoted ±0.9 dB reflects variability across independent single-cell events or across independently fabricated sensors. In biological impedance sensing, cell-to-cell variability and device-to-device variability are often substantial and directly relevant to claimed performance. If the uncertainty instead reflects repeated spectral acquisitions on the same event, it does not quantify generalizability. This matters because the abstract and conclusions frame the gain as a device capability (“maximum gain”) rather than as one illustrative trajectory. Without independent replication, the robustness of the conclusion is materially weakened.\n“Error bars are obtained by averaging between n=4 measurements acquired at different time.” (Figure 3 caption) \nThis caption indicates that the error bars come from four measurements at different times, which is closer to a technical/within-sample repeat than an across-sample replicate. Time-separated measurements on one sample can underestimate uncertainty because they share the same cell, device, medium composition, and setup idiosyncrasies. In addition, time points during adhesion are not statistically independent in the presence of drift, ongoing biological remodeling, and electrode conditioning. Thus, the reported error bars do not capture between-cell variation, which is essential for single-cell sensing claims. The paper also uses these error bars to propagate uncertainty into gain via Eq. 5, so any underestimation carries directly into the headline (20.2 ± 0.9) dB figure. This evidence supports the criticism that the statistical treatment does not match the scope of the claim.\n“Biological replicates are parallel measurements of biologically distinct samples that capture random biological variation, which may itself be a subject of study or a source of noise.” [[6]](#ref6)\nThis definition clarifies that biological replication requires distinct biological samples (e.g., different cells or independently prepared cultures), which is the relevant variability for “single-cell” performance claims. In the reviewed paper, the stated n=4 appears to be repeated measurements at different times rather than distinct cells, so it does not meet this standard. The consequence is that the reported uncertainty cannot be interpreted as capturing biological variability in adhesion/detachment responses. That gap is important for impedance-based biosensors, where biological heterogeneity often sets the practical detection limit and calibration stability. The NIH guidance is not a rigid rule for all studies, but it provides a clear rationale for why the reviewed uncertainty estimate is not aligned with the claim’s implied generality. This strengthens the criticism that the conclusions overreach the presented replication.\n“Technical replicates are repeated measurements of the same sample that represent independent measures of the random noise associated with protocols or equipment.” [[6]](#ref6)\nThis definition matches the reviewed paper’s described approach of repeated spectral acquisitions over time on the same experimental configuration. Technical replicates can quantify instrument noise and short-term measurement variability, but they do not establish reproducibility across new cells/devices. Because the paper’s key conclusion is about sensor gain for single-cell sensing, the most relevant uncertainty includes biological variability (cell positioning, adhesion morphology, membrane properties) and fabrication variability (channel thickness, contact resistance). Technical replication cannot substitute for this, and presenting it as ±0.9 dB can mislead readers about robustness. The evidence therefore supports the criticism that the treatment of uncertainty is not appropriate for the scope of the performance claim. This issue is significant because it directly affects the trustworthiness of the paper’s main quantitative result.\n\nReferences:\n[6] [NIH, “Rigor and Reproducibility Training Module 4: Biological and Technical Replicates” (PDF)](https://grants.nih.gov/policy/reproducibility/training/biological-technical-rep.pdf)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|GPT|4", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "The paper claims that the reported gain materially improves measurement conditions (noise pickup and digitization), but it provides no noise spectra, noise floor, or SNR comparisons, which undermines the reliability of the conclusion that the OECT architecture is “powerful” for single-cell impedance sensing.\n\n“Such an improvement is significant and facilitates measurement conditions regarding noise pickup and digitization, making OECT amplified impedance sensors a powerful tool for a new era of cell-substrate adhesion experiments with a single cell resolution.”\nThis sentence makes a practical instrumentation claim (noise pickup/digitization) that goes beyond reporting a gain ratio. Gain alone does not determine SNR: the device and readout can amplify both signal and noise, and OECTs can introduce additional low-frequency noise components. The manuscript does not report any noise measurements (e.g., current noise spectral density, gate-referred voltage noise, or SNR before/after amplification) for either configuration. It also does not specify the digitization constraints (ADC resolution, dynamic range, or input-referred noise) that would make the gain translate into easier digitization. Therefore, the conclusion that measurement conditions are improved is not supported by presented data. This evidence supports the criticism that the claim over-interprets gain as SNR improvement without the necessary noise characterization.\n“While much emphasis has been placed on analyzing and maximizing the OECT signal, noise has been mostly ignored, although it determines the resolution of the sensor. The major contribution to the noise in sensing devices is the 1=f noise, dominant at low frequency.” [[3]](#ref3)\nThis external source explicitly cautions that OECT sensor performance cannot be assessed from signal magnitude alone because noise sets resolution, especially at low frequencies where many biosensing dynamics occur. The reviewed paper’s maximum gain is reported at 625 Hz, a regime where flicker noise can still be relevant and where OECT operation is often constrained by ionic/electrochemical dynamics. Without noise spectra or an SNR calculation, it is impossible to know whether the 20 dB gain translates into a 20 dB SNR improvement, a smaller improvement, or even a degradation. The cited work provides a concrete methodological expectation in the OECT sensing literature: quantify noise to support claims about resolution. The reviewed paper does not do this, yet it makes strong claims about “noise pickup and digitization.” This mismatch is a major conclusion-level problem rather than a cosmetic omission.\n“Although the device response to analytes can be directly monitored by measuring steady-state channel currents of the devices, it is challenging to obtain stable signals with high signal-to-noise ratios.” [[4]](#ref4)\nThis sentence motivates why AC/OECT sensing papers often discuss stability and SNR explicitly, rather than inferring improved measurement quality from gain alone. The reviewed paper positions itself as providing quantitative guidelines and an optimized geometry for single-cell sensing, so it is reasonable to expect a comparable SNR-oriented evaluation. In particular, if the authors claim improved “digitization,” they should show that the readout is limited by input-referred noise or quantization and that gain addresses this limitation. The cited work also highlights that AC approaches can improve stability and sensitivity, which suggests a natural benchmark for the reviewed manuscript’s claims. Without such benchmarking, the conclusion about measurement-condition improvement remains speculative. This evidence supports the criticism that the paper’s practical claims are not backed by the type of data commonly used to justify them.\n“Microfabricated PEDOT:PSS OECTs on parylene substrates were placed on the surface of the brain of rat models of epilepsy and shown to record seizures with a signal-to-noise ratio that was over 20 dB higher than that of PEDOT:PSS electrodes.” [[1]](#ref1)\nThis example shows how strong claims about improved recording quality can be supported: by reporting an explicit SNR comparison and quantifying the improvement in dB. The reviewed paper similarly reports an improvement of ~20 dB, but it reports it as a gain ratio derived from sensitivity, not as an SNR measurement. The comparison illustrates that the field has established precedents for demonstrating measurement-quality improvements with noise-aware metrics, particularly when making “amplification” claims. Because the reviewed manuscript’s conclusion is framed in similarly strong terms (“powerful tool”), the absence of SNR evidence is conspicuous and weakens the conclusion’s credibility. The evidence does not imply the reviewed gain cannot improve SNR, only that the manuscript has not demonstrated it. Thus, the claim about noise pickup/digitization is not adequately supported.\n\nReferences:\n[1] [Rivnay et al., “Organic Electrochemical Transistors” (review/chapter PDF, Cambridge repository)](https://www.repository.cam.ac.uk/bitstreams/4589a1c1-5616-4ae2-9e3a-37014ab7389c/download)\n[3] [Stoop et al., “Charge Noise in Organic Electrochemical Transistors” (Phys. Rev. Applied 7, 014009 (2017) PDF)](https://www.dora.lib4ri.ch/empa/islandora/object/empa%3A13550/datastream/PDF/Stoop-2017-Charge_noise_in_organic_electrochemical_transistors-%28published_version%29.pdf)\n[4] [Wang et al., “AC Measurements Using Organic Electrochemical Transistors for Accurate Sensing” (ACS Appl. Mater. Interfaces, 2018; abstract via PubMed)](https://pubmed.ncbi.nlm.nih.gov/28846372/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "The paper uses a dielectric microparticle to simulate a single cell for impedance sensing, but fails to adequately justify this approximation, particularly regarding the frequency-dependent impedance characteristics of biological cells.\n\n\"We note that in first order approximation a similar response is expected when a biological cell adheres to the sensor surface.\"\nThis statement oversimplifies the complex impedance behavior of biological cells. While a dielectric microparticle behaves as an insulator across the frequency spectrum, a biological cell consists of a conductive cytoplasm enclosed by a capacitive membrane. At low frequencies, the membrane impedance is high, and the cell may behave similarly to an insulator. However, at higher frequencies (typically >10 kHz), the membrane capacitance shorts, allowing current to flow through the cell interior, which significantly alters the impedance response compared to a solid dielectric particle.\n\"The experiment was repeated at 5 different frequencies (117, 330, 1170, 3330, and 11700 Hz) both in the OECT and in the microelectrode configurations.\"\nThe frequency range used in the experiment extends up to 11.7 kHz and the single cell detection experiment goes up to 100 kHz (\"swept between 10 and 10^5 Hz\"). In this frequency range, the beta dispersion of cells (due to membrane polarization) becomes relevant, and the impedance of a cell deviates from that of a simple dielectric sphere. The paper does not discuss this limitation or provide data to show that the microparticle model remains valid at the higher end of their frequency range.\n\"The opacity spectra for RBCs and polystyrene spheres overlap at low frequencies, but they are clearly differentiable at high frequencies\" [1]\nThis literature demonstrates that while cells and dielectric beads may have similar impedance at very low frequencies, their responses diverge significantly as frequency increases due to the capacitive nature of the cell membrane. The paper's failure to account for this divergence undermines the validity of the microparticle model for the entire frequency range studied.\n\nReferences:\n[1] https://onlinelibrary.wiley.com/doi/10.1002/cyto.a.20141", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "The mathematical model used to describe the OECT response is oversimplified as it assumes a constant transconductance derived from DC characteristics, neglecting the frequency dependence of transconductance due to ionic transport limitations.\n\n\"For the impedance sensing we are interested in the AC response of the transistor and we express the AC current flowing in the OECT channel as Ich,AC = gm,AC*VG*,AC. Following Bernards model, gm,AC can be expressed as gm,AC^lin = -W/L µp cv t VD,DC\"\nThe Bernards model used here assumes that the transconductance is constant and determined by the DC parameters (mobility, capacitance, geometry). However, it is well-established in the literature that OECT transconductance is frequency-dependent and rolls off at higher frequencies due to the limited speed of ionic injection into the channel volume. By using a static transconductance value, the model fails to accurately capture the dynamic response of the OECT, particularly near and above the cutoff frequency where the amplification gain is most critical.\n\"Beyond the maximum, a smaller decrease in sensitivity is observed until it settles to a constant value for high frequencies.\"\nThe paper observes a decrease in sensitivity at high frequencies but attributes it solely to the circuit impedance (electrolyte resistance). It does not explicitly model the intrinsic frequency dependence of the OECT transconductance itself. A more accurate model would include the frequency-dependent nature of the volumetric capacitance or a frequency-dependent transconductance term to fully explain the roll-off behavior.\n\"The performance of organic electrochemical transistors (OECTs) is fundamentally constrained by a trade-off between transconductance and temporal response.\" [2]\nThis reference highlights that the transconductance of OECTs is not constant but depends on frequency, often decreasing significantly at higher frequencies. The paper's model does not account for this fundamental limitation, which may lead to an overestimation of the theoretical gain at higher frequencies.\n\nReferences:\n[2] https://www.researchgate.net/figure/Frequency-dependence-of-the-transconductance-The-device-was-biased-with-V-D-14-A-06-V_fig1_324078891", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "The single-cell detection experiment relies on a very limited sample size (potentially a single cell) without sufficient statistical analysis of cell-to-cell variability or device-to-device reproducibility.\n\n\"An optical image of the final experimental configuration is reported in Figure 3a, showing a single T98G cell positioned at the center of the PEDOT:PSS channel.\"\nThe paper presents results for \"a single T98G cell\" and does not explicitly state how many different cells were measured to obtain the reported sensitivity and gain values. The phrasing suggests that the data might be from a single successful experiment. Without measuring multiple cells and reporting the variance, it is impossible to determine if the reported gain of 20.2 dB is representative of the method or an outlier.\n\"To provide a direct comparison between the sensing performances, we averaged the current amplitudes acquired when the cell is detached (t<30 min and t=240 min) and attached (120<t<180 min), and we subtracted the resulting values to calculate the experimental sensitivity for both devices.\"\nThe averaging described here is over time points for a single experimental run, not over multiple cells or devices. This approach reduces measurement noise for that specific run but does not address biological variability or device reproducibility. A robust study should include statistics from multiple independent experiments with different cells and devices.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|82|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb82", "comment": "It is mentioned several times that there is efficient heath sink due to the Silicon substrate. However, the heat spreading from the diode to the silicon substrate is not clear. Please add the clarification of the heat spreading mechanisms and potential limitations.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|82|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb82", "comment": "The authors should specify the limits on current injection and highest output power that is possible to extract out of the LED.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|82|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb82", "comment": "Unless I overlooked it, the manuscript does not specify at which temperature were the measurements carried out. Furthermore, it would be highly complementary to measure the light emission/EQE at different temperatures. The authors must consider additional measurements at different temperatures to have additional insights on the physical mechanisms limiting efficiency.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|82|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb82", "comment": "The authors should mention the potential modifications of the structure to achieve higher optical output powers.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|82|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb82", "comment": "The authors mentioned that the LED structures on multiple chips do not vary significantly. This variance should be quantified to give insights on the reproducibility of the fabrication process (especially the reproducibility of the silicon filament formation is a concern to me).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|82|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb82", "comment": "The authors mentioned “In our previous work, we have shown that vertical pn junctions with top metal contact can support high injection current while also lower the device footprint compared to lateral junctions.32 However, the opaque metal contact leads to significant shadowing if the emission area shrinks to a comparable size. ... Compared with the work on the smallest CMOS emitters,32 the emission area is 2 orders of magnitude smaller and the average intensity is approximately doubled”. From this description, the difference between the present work and the previous work in 32 is that the top contact is replaced by a n-poly-Si. Is there any other significant difference? Please clarify more details about this. What is the major reason for the 2 orders of magnitude improvement?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|82|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb82", "comment": "The present LED emits with the emission spectrum centered around 1100 nm. Please tell a little more details about the potentials the present LED for various applications.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|82|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb82", "comment": "Is the wavelength tunable?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|82|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb82", "comment": "The authors described the formation of the Si filament whose size is about usually sub-100 nm. Is the position of the Si filament controllable, or is it a kind of random? Is there any influence on the device performance?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|82|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb82", "comment": "Could this micro-LED be modulated fast? It will be very nice if the authors can give a comment and explanation on this.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|82|Claude|1", "source": "prb", "split": "test", "paper_id": "prb82", "comment": "The paper reports a sub-wavelength Si LED based on gate oxide breakdown as its operational mechanism, yet fails to adequately characterize or address the inherent reliability and lifetime limitations of this approach, despite presenting evidence of significant performance degradation (~25% power loss after ~10^5 on/off cycles) in the supplementary materials.\n\n\"In our test, the substrate was biased at 6.0 V with the poly-Si grounded to introduce gate oxide breakdown. We observed that the current rapidly increased from pA to mA and was stabilized within 1 min.\"\nThe device fundamentally relies on gate oxide breakdown, which is a damage-inducing process. While the authors describe this as a mechanism to create a Si filament contact, gate oxide breakdown is well-established in the semiconductor reliability literature as a failure mechanism that inherently leads to progressive degradation over time. The formation of a conductive filament through the oxide represents permanent structural damage that can propagate, as indeed observed in this work. This operational principle raises fundamental concerns about long-term device stability that are not adequately addressed in the main text.\n* Quote (Supplementary S6): \"After the test, the SMF-coupled power dropped by approximately 25%. As we mentioned in the main text, this is probably due to the lateral propagation of the breakdown site which also leads to the forward bias lowering.\"\nThe supplementary materials reveal substantial performance degradation (25% power loss) after approximately 10^5 on/off switching cycles. This level of degradation after relatively limited cycling is significant and raises serious questions about the practical applicability of the device. The authors acknowledge this is \"probably due to the lateral propagation of the breakdown site,\" which indicates an ongoing damage mechanism. However, no quantitative lifetime analysis, accelerated testing, or comparison with reliability standards (e.g., L70 lifetime metrics commonly used for LEDs) is provided. For a technology claiming CMOS compatibility and potential applications, this omission significantly undermines the validity of the work.\n\"The breakdown process is usually referred as hard breakdown. Microscopically, when high-voltage gate bias is applied, traps form and a conduction path is created. Near this path, the gate current leads to thermal damage which creates more traps.\"\nThe authors explicitly describe a positive feedback mechanism where current flow leads to thermal damage that creates more traps. This is characteristic of time-dependent dielectric breakdown (TDDB), a well-known reliability concern in CMOS technology. According to semiconductor reliability literature, gate oxide breakdown sites can continue to evolve under electrical stress, leading to further degradation. The paper does not provide any accelerated lifetime testing or reliability modeling to quantify the expected device lifetime, which is standard practice for establishing the viability of new device technologies.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|82|Claude|2", "source": "prb", "split": "test", "paper_id": "prb82", "comment": "The paper reports characterization of only five devices across different chips, which show substantial performance variation (±20% in SMF-coupled power), with one device exhibiting notably inferior characteristics. This limited sample size and significant variation undermine the reproducibility and generalizability of the reported results.\n\n* Quote (Supplementary S5): \"In Fig. S5, SMF-coupled power and forward bias voltage versus current of five LEDs on different chips are presented. These curves were measured right after gate oxide breakdown. In Fig. S5 (a), three curves almost overlap while the other two are approximately ±20% deviated.\"\nA device-to-device variation of ±20% is substantial for a precision light emitter, particularly for applications requiring consistent illumination such as the demonstrated holographic microscopy. The fact that only 5 devices were tested is statistically insufficient to establish reproducibility, as it does not provide meaningful confidence intervals or allow for proper statistical analysis. Standard practices in device physics and semiconductor manufacturing typically require larger sample sizes and multi-wafer/multi-lot testing to establish process stability and yield.\n* Quote (Supplementary S5): \"The variance is probably due to the spatial randomness of the breakdown site within the STI opening area (≈0.3 μm²). For example, if the breakdown happens near the interface of the n well and the STI, a current leakage path may form. This is likely the situation of LED1 with the lowest SMF-coupled power since it also has the lowest forward bias.\"\nThe authors acknowledge that the device performance depends on the random spatial location of the breakdown site, which is inherently stochastic. This randomness fundamentally limits the controllability and reproducibility of the device fabrication process. The fact that one device (LED1) shows anomalous behavior attributed to proximity to the STI interface suggests that the yield of high-performing devices may be low, but no yield statistics are provided. For claims of CMOS compatibility and potential scalability, this level of process randomness is a significant concern.\n\"In the main text, we mainly present the device performance of LED2 after the robustness test.\"\nPresenting data primarily from a single device (LED2) after it has undergone degradation from 10^5 cycles further limits the representativeness of the reported results. The selection of which device to highlight and the decision to present post-degradation data as representative raises questions about the generalizability of the performance metrics claimed in the paper.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|82|Claude|3", "source": "prb", "split": "test", "paper_id": "prb82", "comment": "The key claim of sub-wavelength emission area (<0.14 μm² or Ø400 nm) relies on PSF deconvolution with Gaussian assumptions, but when the deconvolved size approaches the PSF width (784±50 nm in x, 740±46 nm in y), the uncertainty in the emission area estimate becomes substantial and may not be adequately reported.\n\n* Quote (Supplementary S2): \"The Point-spread-function (PSF) of the microscope was calibrated using a reflective target sample with sharp edges. The edges were fit into erf functions which were used to extract the full-width-half-maximum (FWHM) of the PSF.\"\nWhile the PSF calibration methodology is reasonable, the PSF FWHM of 784±50 nm in x and 740±46 nm in y means that the deconvolved emission sizes (down to 330-350 nm as reported in Supplementary S3) are approximately 42-47% of the PSF FWHM. At this ratio, deconvolution becomes increasingly sensitive to noise, PSF measurement errors, and deviations from the assumed Gaussian shape. Standard imaging practice suggests that reliable deconvolution typically requires the true object size to be comparable to or larger than the PSF, and sub-PSF deconvolution carries significant uncertainty.\n* Quote (Supplementary S4): \"We assume both the emission pattern and the PSF are Gaussian-shaped and the deconvolved FWHM can be thus computed as: FWHM_x/y,decon = √(FWHM_x/y,fit² - FWHM_x/y,PSF²)\"\nThis simple quadrature subtraction formula is only valid when both the emission pattern and PSF are perfectly Gaussian, which is an approximation. The formula also becomes numerically unstable when the measured FWHM approaches the PSF FWHM, as small errors in either measurement propagate to large errors in the deconvolved size. The error bars shown in Figure 2(h) grow substantially at higher currents where the emission is most confined, but the methodology for propagating these uncertainties through the quadrature formula to the final emission area claim is not fully transparent.\n\"The deconvolved emission area and the spatial intensity versus the current. The deconvolution results are based on the FWHM of the PSF of the microscope.(784±50 nm in x and 740±46 in y. See supplementary S2 S4)\"\nGiven PSF uncertainties of approximately 6% in each dimension, the propagated error in the deconvolved area at the smallest sizes becomes significant. For example, when the measured FWHM is close to the PSF (e.g., 1.1× PSF), a 6% error in PSF translates to a much larger relative error in the deconvolved size. The paper's claim of emission area smaller than 0.14 μm² should include a more rigorous uncertainty analysis that accounts for these effects, particularly since this sub-wavelength emission area claim is central to the paper's novelty.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|82|GPT|1", "source": "prb", "split": "test", "paper_id": "prb82", "comment": "This paper’s core device operation mechanism depends on intentionally inducing hard gate-oxide breakdown to create a conductive filament, which materially compromises validity for a “CMOS platform” integrated light source because hard breakdown is a catastrophic reliability event with inherently stochastic location and measurable degradation, and the manuscript does not provide a reliability/variability analysis sufficient for its integration claims.\n\n“The Si filament is formed by applying electrical stress after the fabrication. Specifically, we apply forward bias between the n+ and p+ terminals in the break-down mode such that the substrate is biased at 6.0 V. The high electrical field introduces gate oxide breakdown, and a conductive path (filament) forms between the substrate and the n+ terminal. Such high power breakdown is categorized as hard breakdown, which provides intense light emission and short filament.”\nThis passage states that the LED is not a conventional, intact CMOS junction emitter but rather a device intentionally driven into gate-oxide hard breakdown to form a filamentary conductive path. In mainstream CMOS reliability practice, “hard breakdown” is treated as a failure mode because it creates a low-resistance leakage path and can compromise circuit functionality and lifetime. Making this breakdown event the enabling mechanism means the platform claim hinges on post-breakdown electrical integrity, variability control, and long-term stability, not just optical output. However, the main text does not report standard reliability metrics for breakdown-based devices (e.g., breakdown distributions, post-breakdown leakage evolution under bias/temperature, or failure modes impacting nearby circuitry). Because the breakdown event is singular and stochastic, it also raises questions about wafer-level yield and uniformity that must be quantified to support a CMOS-integration conclusion. Without such data, the central mechanism is insufficiently validated for the stated integration context.\n“In Fig. S5, SMF-coupled power and forward bias voltage versus current of five LEDs on different chips are presented. These curves were measured right after gate oxide breakdown. In Fig. S5 (a), three curves almost overlap while the other two are approximately \\( \\pm 20\\% \\) deviated. The variance is probably due to the spatial randomness of the breakdown site within the STI opening area (\\( \\approx 0.3\\ \\mu m^2 \\)). … In Fig. S6, we plot the performance of LED2 … after on/off switch for \\( \\approx 10^5 \\) times as a robustness test. After the test, the SMF-coupled power dropped by approximately 25%.”\nThe supplement explicitly attributes device-to-device performance spread to the randomness of the breakdown site, i.e., the key enabling event is not deterministically positioned or controlled. A ±20% variation across only five samples already indicates significant variability for a component the paper positions as a practical on-chip light source. More importantly, the robustness test reports a ~25% optical-power degradation after ~10^5 switching cycles, showing that the post-breakdown filament continues to evolve under operation. This degradation directly contradicts any implicit assumption that the filament is stable once formed, and it implies that reported performance may drift over time or with usage conditions. The manuscript does not provide failure criteria, longer-term cycling, or environmental stress tests (temperature, humidity, bias stress) that are standard for reliability claims in CMOS contexts. Because the authors “mainly present the device performance of LED2 after the robustness test,” the headline performance is already tied to a degraded state whose stability is not established.\n“Dielectric breakdown is a sudden and catastrophic increase in the conductivity of an insulator caused by electrical stress.” [[1]](#citation-1)\nThis definition from a recent review frames dielectric breakdown as an abrupt, catastrophic conductivity change rather than a benign operating regime. The paper’s approach intentionally triggers this event in the gate oxide to create the conductive filament, so it inherits the reliability risks associated with breakdown physics by construction. In conventional CMOS technology, such a catastrophic transition is precisely what reliability qualification aims to avoid during normal operation. Using it as the operating principle raises the bar for demonstrating controlled formation, repeatability, and stability across many devices and wafers. The manuscript does not provide evidence that breakdown can be confined without collateral damage or unacceptable leakage, especially when integrated near mixed-signal circuits as claimed. Therefore, the literature context supports that the paper’s reliance on hard breakdown is a major validity concern unless accompanied by substantially stronger reliability data.\n“After breakdown a link of electron traps is formed in the gate oxide which connects the gate with the substrate.” [[2]](#citation-2)\nThis sentence describes the physical meaning of post-breakdown conduction as a trap-mediated link through the gate oxide, consistent with the filamentary picture invoked by the authors. It emphasizes that the breakdown path is fundamentally a damaged-oxide conduction channel, not a reversible or engineered semiconductor junction. Such trap-assisted conductive links are known to have variability in geometry and resistance and can evolve with stress, aligning with the variance and degradation the supplement reports. In this context, claims of stable optical performance and clean electrical behavior require explicit characterization of post-breakdown conduction pathways and their evolution. The reviewed manuscript does not quantify how this breakdown link affects parasitic currents, noise, or interference with neighboring electronics on the same CMOS die. As a result, the literature supports that the paper’s integration and robustness conclusions are under-justified.\n\nReferences:\n[1] [A. Padovani et al., “Dielectric breakdown of oxide films in electronic devices” (review, PDF)](https://discovery.ucl.ac.uk/10196865/1/Shluger_Dielectric%20breakdown%20of%20oxide%20films%20in%20electronic%20devices_AAM.pdf)\n[2] [V. E. Houtsma, “Gate Oxide Reliability of Poly-Si and Poly-SiGe CMOS devices” (PhD thesis, PDF)](https://ris.utwente.nl/ws/portalfiles/portal/6076619/t0000011.pdf)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|82|GPT|2", "source": "prb", "split": "test", "paper_id": "prb82", "comment": "The paper draws strong conclusions that its sub-wavelength Si LED provides spatially coherent illumination adequate for lensfree holographic microscopy, but it does not quantify spatial coherence (or distinguish it from temporal coherence) in a way that would support the holography claims given the reported broad emission bandwidth and the lack of coherence/visibility measurements across the stated centimeter-scale field of view.\n\n“Importantly, our LED emits spatially coherent light with low power. This property is not only useful for modern silicon photonics but also enables new applications like holographic microscopy and endoscopic imaging. … Since the emission is already from a sub-wavelength region, the LED can be treated as its own spatial filter.”\nThese sentences elevate spatial coherence from an observation to a central enabling claim for multiple downstream applications, including holographic microscopy. However, the manuscript does not provide a quantitative spatial-coherence characterization (e.g., fringe visibility versus baseline, mutual coherence function, or an equivalent coherence-area estimate at the sample plane). Treating sub-wavelength emission size as a “spatial filter” is an assertion that requires experimental confirmation in the actual imaging geometry because effective coherence depends on source size, propagation, and any multimode/extended emission contributions. In practice, lensfree holography performance is sensitive to coherence across the full illuminated area, not only at one location or for a single qualitative hologram. Without reporting coherence metrics, it is not possible to assess whether the observed holograms are robust to different samples, distances, or fields of view. This gap weakens the robustness of the paper’s holography-related conclusions.\n“In Fig. 1 (e) inset, we present the output hologram of the LED. … The presence of these bright rings verifies that the spatial coherence is high enough to compensate for the broad emission spectrum.”\nThe paper uses the presence of “bright rings” in one hologram as the key validation for spatial coherence and further claims it compensates for the “broad emission spectrum.” A single example hologram with visible fringes is not a quantitative coherence test, because fringe visibility can remain nonzero under partial coherence and depends strongly on object type, distance, and exposure/processing. Moreover, the statement conflates different coherence limitations: spatial coherence governs lateral interference across the aperture, while spectral bandwidth governs temporal coherence and the allowable optical path differences; demonstrating one does not establish the other. The manuscript does not report fringe visibility, reconstructed resolution, or a controlled coherence experiment (e.g., varying source-to-sample distance or introducing known path differences) that would substantiate the “high enough” claim. Because the holography application is highlighted as a major significance claim, this lack of quantitative support is a substantial methodological weakness.\n“The spectral full-width-half-maximum (FWHM) of the emission increases monotonically from approximately 150 nm to 190 nm (Fig. 1 (f) inset).”\nThis quote documents that the source has a very broad emission bandwidth, which is directly relevant to holographic interference robustness because broader spectra generally reduce the temporal-coherence length. The paper does not report how the hologram geometry (source–sample–sensor distances, path differences, or spectral filtering) is chosen to ensure adequate fringe contrast under this bandwidth. In addition, the manuscript does not provide an analysis of how the bandwidth-induced fringe washout might vary across the stated large field of view or for thicker/3D samples, which are common in lensfree holography. The claim that spatial coherence “compensates” for broad spectrum is therefore not supported by an accompanying model or measurement that accounts for bandwidth effects. In standard practice, authors either constrain path differences, narrow the spectrum, or explicitly model partial coherence to justify reconstructions. The absence of such quantitative treatment makes the holography conclusion insufficiently substantiated.\n“However the compactness is impacted by the need of obtaining a certain degree of spatial coherence.” [[3]](#citation-3)\nThis peer-reviewed lensfree holography article emphasizes that spatial coherence is a concrete, design-limiting requirement, not a qualitative attribute that can be inferred from a single image. In that literature, achieving adequate coherence is typically handled via explicit geometric constraints and/or spatial filtering (e.g., source distance and pinholes) and is discussed quantitatively in relation to field of view and sample constraints. In contrast, the reviewed paper does not provide comparable quantitative coherence characterization or design rules tied to its LED’s emission properties. The mismatch between the field’s common practice (explicitly addressing coherence as a limiting parameter) and the paper’s qualitative validation undermines confidence in the generality of its holographic-microscopy claims. Given that holography is presented as a key application enabled by the device, the absence of such quantitative coherence analysis is a significant shortcoming.\n\nReferences:\n[3] [M. Rostykus et al., “Compact in-line lensfree digital holographic microscope,” Methods (2018) (PMC)](https://pmc.ncbi.nlm.nih.gov/articles/PMC5869056/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|82|GPT|3", "source": "prb", "split": "test", "paper_id": "prb82", "comment": "The manuscript’s key quantitative results on “sub-wavelength” emission area and derived spatial intensity rely on Gaussian PSF/emission assumptions and a simple FWHM-based deconvolution that is not validated for the reported imaging system, which materially weakens the reliability of the claimed emission-area shrinkage and intensity values.\n\n“We assume both the emission pattern and the PSF are Gaussian-shaped and the deconvolved FWHM can be thus computed as\n\n\\[\nFWHM_{x/y,decon} = \\sqrt{FHHM_{x/y,fit}^2 - FHHM_{x/y,PSF}^2} \\tag{Eq. S2}\n\\]\n\nThe deconvolved FWHMs are used to estimate the emission area in Fig. 2 (h).”\nThis is the central methodological step behind the paper’s sub-wavelength area claim, and it explicitly depends on both the emitter and microscope PSF being Gaussian-shaped. In microscopy, real PSFs are diffraction patterns with sidelobes, and real emitters can be non-Gaussian or multi-component, especially when the paper also reports a “diffusive background” and metal-fill shadowing. A scalar FWHM subtraction loses shape information and can be highly sensitive when the fitted FWHM is close to the PSF FWHM, which is exactly the regime the paper operates in (sub-micron spots with ~0.7–0.8 µm PSF FWHM reported in the main text). The manuscript does not show a calibration demonstrating that Eq. S2 reproduces known sub-resolution objects or that the Gaussian assumption is valid across currents. Without such validation, the deconvolved widths—and therefore emission areas and intensities derived from them—are not robustly supported. This directly affects the paper’s headline “sub-wavelength” quantitative claims.\n“The emission area is estimated by deconvolving the spatial FWHM of the emission spot from the Gaussian fit using the independently measured point-spread-function (PSF) of the microscope. … From 1 mA to 6 mA, the emission area shrinks from approximately 0.30 ± 0.12 \\( \\mu \\)m\\(^2\\) to 0.09 ± 0.04 \\( \\mu \\)m\\(^2\\). … At 6 mA, the intensity is approximately 102 ± 48 mW/cm\\(^2\\).”\nThese are quantitatively prominent results used to argue sub-wavelength confinement and high intensity, but they inherit all assumptions and errors of the deconvolution procedure. The reported uncertainties are large relative to the values (e.g., 0.09 ± 0.04 µm² and 102 ± 48 mW/cm²), indicating that systematic modeling error could be comparable to the stated error bars. Because the emission area is not directly measured but inferred from FWHM differences, any PSF mis-modeling, aberration, or non-Gaussian tails will bias the area and propagate multiplicatively into the intensity estimate. The paper also notes that emission outside a limited region is “shadowed by metal fill,” which means the observed image may not represent the full emission distribution needed for a faithful deconvolution. As a result, the reported area shrinkage and intensity values are not sufficiently method-validated to serve as strong quantitative evidence for the claimed confinement mechanism. This weakens downstream comparisons (e.g., “2 orders of magnitude smaller area”) that rely on these numbers.\n“Rather, light waves converge and interfere at the focal point to produce a diffraction pattern of concentric rings of light surrounding a central, bright disk, when viewed in the x-y plane.” [[4]](#citation-4)\nThis microscopy reference describes the PSF as an Airy-like diffraction pattern rather than a Gaussian, highlighting a direct mismatch with the paper’s Gaussian-PSF assumption. While Gaussians can be convenient approximations near the central lobe, the presence of rings and non-Gaussian tails is precisely what can bias FWHM-based deconvolution when estimating sub-resolution sizes. The reviewed manuscript does not provide evidence that its measured PSF is well-approximated by a Gaussian across the relevant intensity range, nor does it quantify how sidelobes or aberrations affect its fitted widths. Because the claimed emission area is obtained by subtracting PSF width in quadrature, even modest deviations from Gaussian behavior can lead to substantial area errors. Standard deconvolution practice typically uses measured or modeled PSFs in full (not only FWHM) and validates size estimates with known calibration objects. The cited reference therefore supports that the paper’s simplified deconvolution approach is methodologically fragile for the reported quantitative claims.\n“The product of two Gaussian functions is a Gaussian, and the convolution of two Gaussian functions is also a Gaussian, with variance being the sum of the original variances: \\(\\sigma^2 = \\sigma_1^2 + \\sigma_2^2\\).” [[6]](#citation-6)\nThis property explains why quadrature addition/subtraction of widths is only theoretically justified when both the object and the PSF are well-modeled as Gaussians. The reviewed paper applies this relationship at the level of FWHM (Eq. S2), which is equivalent to the variance relationship only under the Gaussian assumption. If either the emission spot or the PSF deviates from Gaussian shape (e.g., Airy-like diffraction rings, asymmetric aberrations, or multi-component emission), the variance-additivity model breaks and Eq. S2 can produce biased or even nonphysical estimates. The manuscript does not present residual analyses or alternative models to justify that the Gaussian approximation is adequate in the regime where it claims sub-wavelength sizes. Because the emission area and intensity claims are central to significance, the lack of validation of the required Gaussian conditions is a major methodological gap. The cited statement clarifies that the paper’s deconvolution formula is not a general deconvolution method but a special-case identity with restrictive assumptions.\n\nReferences:\n[4] [ZEISS Microscopy Online Campus, “The Point Spread Function”](https://zeiss-campus.magnet.fsu.edu/articles/basics/psf.html)\n[6] [“Gaussian function,” Wikipedia](https://en.wikipedia.org/wiki/Gaussian_function)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|82|GPT|4", "source": "prb", "split": "test", "paper_id": "prb82", "comment": "The paper’s external quantum efficiency (EQE) and “no thermal droop” conclusion are not robust because the reported EQE is explicitly computed only from the fitted central spot while neglecting background emission, making it non-comparable to standard EQE definitions and potentially biasing the EQE-versus-current trend used to support the droop claim.\n\n“In Fig. 2 (e), we present the n+/n emission power and the external quantum efficiency (EQE) versus the current. The emission power was evaluated by integrating the Gaussian fit of the spot … At 6 mA, the n+/n emission power and the EQE are approximately 94.0 pW and \\( 1.4 \\times 10^{-8} \\), respectively. … Note that the EQE shows no thermal droop even when the current density is above 2 MA/cm\\(^2\\) … This is mainly because the LED is embedded in the Si substrate which is an efficient heat sink.”\nThe paper links a monotonic EQE curve to a strong physical conclusion (“no thermal droop”) and a causal mechanism (efficient heat sinking), but the EQE is computed only from the “spot” component of a fitted model rather than the total emitted photon flux. The quoted EQE value is extremely small (10⁻⁸), so systematic errors in background separation, calibration, and collection geometry can dominate the relative uncertainty even if fit-parameter confidence intervals are reported. The droop inference assumes that the reported spot-based EQE tracks the true external efficiency of the device, yet the paper does not show that background emission is negligible or current-invariant. The heat-sink explanation is also not backed by a direct thermal measurement of junction/filament temperature under bias; it is inferred indirectly from spectral behavior elsewhere. Standard droop analyses in LEDs typically control for total emitted power and thermal conditions (or explicitly measure temperature) to support such conclusions. As presented, the droop conclusion is therefore not sufficiently supported by the methodology described.\n“Note that here EQE only accounts for the emission of the spot while the background is neglected.”\nThis figure-caption statement explicitly acknowledges that the reported “EQE” excludes background emission by design. In standard usage, EQE refers to the ratio of total emitted photons leaving the device to injected electrons; restricting the numerator to a selected spatial component makes the metric a partial, application-specific efficiency rather than an external quantum efficiency of the emitter. Because the background is physically part of the device emission (and the paper elsewhere reports a background extending ±10 µm), excluding it can change the apparent current dependence and thus the presence or absence of “droop.” The manuscript does not demonstrate that the neglected background is constant with current or quantify how much total power it carries relative to the spot. In addition, neglecting background while using the result to claim high-current operation without droop risks overstating performance for practical illumination applications that would collect both components. This is a major interpretability issue because it directly affects one of the paper’s highlighted performance conclusions.\n“where the first Gaussian denotes the n+/n spot and the other two terms denote the background.”\nThe supplementary clarifies that the data model explicitly decomposes the measured emission into a spot component and a background component. Given that the background is modeled (not absent), excluding it from the EQE numerator is a methodological choice that should be justified by application-specific collection conditions or by showing it is negligible. However, the paper’s droop and efficiency conclusions are phrased in general terms (EQE, thermal droop), which in the LED literature typically refer to the whole device emission. If the background fraction changes with current, then a spot-only EQE can increase monotonically even if total EQE saturates or decreases, undermining the robustness of the droop claim. The manuscript also does not report uncertainty contributions from this model selection (two-Gaussian + constant decomposition) to the EQE trend, despite the very low absolute EQE values. Without validating that the spot-only metric faithfully represents device-level efficiency, conclusions drawn from it remain unreliable.\n“The external quantum efficiency of the LED takes into account the device design parameters and is simply defined as: photons out … EQE = … electrons in …” [[5]](#citation-5)\nThis lecture material provides a standard definition of LED external quantum efficiency as photons out per electrons in, i.e., a device-level photon-counting metric. The reviewed paper’s EQE explicitly excludes the background component, so it does not match this standard definition unless the paper can show that the background is not “photons out” for the relevant device operation. The same source also emphasizes that practical EQE determination is tied to measuring photon flux from total optical power, which requires accounting for the full emission spectrum and collection conditions. Because the manuscript uses the term “external quantum efficiency” while applying a restricted spatial integration, readers cannot readily compare its EQE to other LEDs or to droop literature that uses the standard definition. This discrepancy affects the interpretability and reliability of the efficiency and droop claims that are central to the paper’s conclusions. Aligning the metric with standard definitions (or renaming it as a partial/spot EQE and reporting total emission separately) would be necessary for robust conclusions.\n\nReferences:\n[5] [MIT OpenCourseWare, “Lecture 19-20: Light Emitting Diodes” (PDF)](https://ocw.mit.edu/courses/3-024-electronic-optical-and-magnetic-properties-of-materials-spring-2013/0ba1a47f71a8843b0e45b9aa2e66a875_MIT3_024S13_2012lec19-20.pdf)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|82|GPT|5", "source": "prb", "split": "test", "paper_id": "prb82", "comment": "", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|82|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb82", "comment": "The paper claims the device is stable, but the supplementary data shows significant degradation (25% drop) after only 10^5 cycles, which contradicts the claim and fails to meet standard reliability criteria for LEDs.\n\n\"After the breakdown, the IV characteristic was stable and showed no obvious hysteresis.\"\nThe main text asserts stability based on IV characteristics immediately after breakdown, implying the device is robust for operation.\n\"After the test, the SMF-coupled power dropped by approximately 25%. As we mentioned in the main text, this is probably due to the lateral propagation of the breakdown site which also leads to the forward bias lowering.\"\nThis admission in the supplementary material (Section S6) directly contradicts the impression of stability given in the main text. A 25% drop in power after only 100,000 on/off cycles is a major failure for a light-emitting device. For context, standard LED reliability testing (e.g., IES LM-80) typically requires at least 6,000 hours of operation [1]. 100,000 cycles, depending on the cycle duration, is likely orders of magnitude shorter than the industry standard for reliability testing.\n\"In Fig. S6, we plot the performance of LED2... after on/off switch for \\( \\approx 10^5 \\) times as a robustness test.\"\nThe use of only 10^5 cycles as a \"robustness test\" is insufficient to demonstrate practical reliability. Without long-term continuous wave (CW) operation data, the claim of a stable, practical emitter is unsupported.\n\nReferences:\n[1] IES LM-80-08 Approved Method: Measuring Lumen Maintenance of LED Light Sources. Illuminating Engineering Society, 2008.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|82|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb82", "comment": "The paper makes a misleading comparison with state-of-the-art Si emitters by focusing on \"intensity\" (power/area) while ignoring the extremely low external quantum efficiency (EQE) and total power, which are critical metrics for practical utility.\n\n\"This LED has high spatial intensity of > 50 mW/cm\\(^2\\) which is comparable with the state-of-the-art Si-based emitters with much larger emission areas.\"\nThis statement is misleading because the \"high intensity\" is primarily a result of the sub-wavelength emission area (< 0.14 \\(\\mu m^2\\)), not high optical power output. The total power is in the picowatt range (94 pW), which is negligible for most non-imaging applications.\n\"At 6 mA, the n+/n emission power and the EQE are approximately 94.0 pW and \\( 1.4 \\times 10^{-8} \\), respectively.\"\nAn EQE of 1.4 x 10^-8 is extremely low, even for silicon LEDs. For comparison, early silicon LEDs reported by Green et al. achieved efficiencies around 10^-2 to 10^-3 [2], and other breakdown-mode devices have reported higher efficiencies. By focusing on intensity, the authors mask the fact that the device is extremely inefficient, converting almost all input power into heat, which is a critical limitation not adequately addressed in the comparison.\n\"The emission area of our LED is the smallest among the reported Si LEDs. The intensity is comparable with other state-of-the-art Si LEDs with much larger emission areas.\"\nThis benchmark (Fig. S4) is selective. A fair comparison would include EQE and total power, which would reveal that this device underperforms significantly compared to the \"state-of-the-art\" references cited (e.g., [2], [3]).\n\nReferences:\n[2] M. A. Green, J. Zhao, A. Wang, P. J. Reece, and M. Gal, “Efficient silicon light-emitting diodes,” Nature 412, 805–808 (2001). https://doi.org/10.1038/35090539\n[3] S. W. Schmitt, K. Schwarzburg, G. Sarau, S. H. Christiansen, S. Wiesner, and C. Dubourdieu, “All-silicon polarized light source based on electrically excited whispering gallery modes in inversely tapered photonic resonators,” APL Materials 8, 061110 (2020). https://doi.org/10.1063/5.0009637", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|82|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb82", "comment": "The paper uses the term \"LED\" (Light Emitting Diode) without sufficient qualification, which is misleading because the device operates based on a destructive gate oxide breakdown mechanism (antifuse) rather than standard minority carrier injection in a pristine p-n junction.\n\n\"In this letter, we report an electrically driven Si light-emitting diode (LED) with sub-wavelength emission area fabricated in an open-foundry microelectronics CMOS platform.\"\nThe term \"LED\" typically implies a diode where light is generated by recombination of injected carriers in a semiconductor bandgap. While the authors claim band-to-band recombination, the device structure and formation rely on \"hard breakdown\" of the gate oxide to form a filament.\n\"In this area, a Si filament is formed in the gate oxide by applying electrical stress. This process is usually referred as hard breakdown.\"\nDevices based on oxide breakdown are distinct from standard LEDs and are often termed \"breakdown emitters\" or \"antifuse\" light sources in the literature [4]. The breakdown process creates a conductive filament whose properties (size, composition, stability) are difficult to control and reproduce, as evidenced by the 20% variance reported in Supplementary S6. Using the unqualified term \"LED\" obscures this fundamental difference in mechanism and reliability.\n\nReferences:\n[4] N. Akil, V. Houtsma, P. LeMinh, J. Holleman, V. Zieren, D. De Mooij, P. Woerlee, A. van den Berg, and H. Wallinga, “Modeling of light-emission spectra measured on silicon nanometer-scale diode antifuses,” Journal of Applied Physics 88, 1916–1922 (2000). https://doi.org/10.1063/1.1305856", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|82|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb82", "comment": "", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "More emphasis should be provided on the importance of monitoring cell adhesion. The state of the art on cell adhesion monitoring should be discussed, pointing out the advantage of the approach herein reported.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "Could the authors report in the introduction a more comprehensive description about ultra sensitive OECT biosensors? Have been ever employed to monitor single cell adhesion?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "Is the Gate leakage correct of the OECT being monitored? Could the authors report the IG vg. Vg curves in Figure 1 along with the output and transfer characteristics of the transistor.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "the authors state that \"The proportionality constant p is independent on the sensor 174 configuration (OECT vs microelectrode) and we obtain its numerical value by fitting the microelectrode impedance spectra \". Could the authors comment in more detail the physical meaning of this parameter?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "At page 8 the authors state \"The factor fOECT in eqn. 1 determines how the gate current is distributed between the source and the drain terminal and is typically assumed to be equal to 0.5 Several studies demonstrate that the fOECT factor is slightly dependent on VD,DC and 215 VG,DC as well as on channel geometry. For this reason, fOECT was not assumed as constant in this experiment, but its value was set for each sensor in order to best fit the experimental data with the model.\" How the authors checked that this does not lead to overfitting? How this value has been selected. Did the author checked that the value assumed in each case are reasonably correct given the experimental conditions?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "Figure 2 does not reports error bars at all. Hoe the repeatability and the reproducibility of the platform has been addressed?", "reviewer_type": "human", "label": "error", "error_type": "Neglect", "label_origin": "expert+llm-filter"}
{"id": "prb|81|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "Hoe the authors ensure that a single cell adhesion has been monitored? Did the monitor independently that a single cell was deposited on the channel of the OECT? could the authors comment more on this aspect?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "Page 2, bottom: When discussing the nanophase network of organic semiconductors and polyelectrolytes, it would be good to mention the role of (primary, secondary) doping and additives (such as DMSO, PEG, etc).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "I’m impressed by the sensitivities that the authors present, given the relatively minimal coverage of the active sensing area by the microparticle or the single cell. The authors do present a qualitative argument (page 6), but I’m interested in some mention of a quantitative argument as well. There is mention of the W/L ratio through the manuscript. Does the relative coverage of the W (or L) match expectations quantitatively? How is that the a nearly uncovered channel (e.g., Fig. 3a) exhibits such a strong change to the presence of the cell? (This might be covered in the referenced literature or distributed through the main and supplementary text, but it would be good to include this argument in the manuscript).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "Following on this comment of cell coverage, I wonder if the authors investigated the OECT channels NOT covered 1 or more cells. Or even better, an OECT channel with a cell just off to the side. This could be a good control experiment to see if the T98G cells might be excreting adhesion substances that could alter the impedance.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "Does the trypsin treatment (page 11) affect the OECT/microelectrode in any way? Relating to the previous comment, could it be “cleaning off” the channel of cell-excreted adhesion substances?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "The derivation of Eqns. 3 and 4 is not directly obvious from “the two AC current contributions and differentiation”. Since these equations are the real contribution of this manuscript, I would spend more space here elaborating the derivation so that all readers can clearly see the work.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "Likewise, derivation of Eqn. 5 is not directly obvious. In addition, I would further expand Eqns. 3 and 4 until the frequency ( \\omega ) terms were visible. Since the remainder of the work focuses on frequency response, it would be very helpful to directly see s_ch and s_\\mu E as functions of  \\omega .", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "In Figure 3b, the arrow indicating trypsin treatment appears at the timepoint after the drain current starts to increase again. Is this correct?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "Page 2, line 26: “mixed ionic and electronically” → “mixed ionic and electronic”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "Page 3, line 2: “this properties combination” → “this combination”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_2|10", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "Page 3, line 32: I would recommend defining the transfer function here, e.g., “I_DS as a function of V_G”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_2|11", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "Figure 1b: Shouldn’t the left and right contacts of the microelectrode be connected by a circuit line? On page 6, line 9, the authors state that they’re short circuited.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_2|12", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "Figure 1e: It would be nice to see the current amplitude as relative changes or normalized to initial value. This could help see the difference between OECT and microelectrode. Perhaps on the right axis?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_2|13", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "Throughout: values do not need to be in parentheses. For example, “(0.059±0.002) nA/ \\Omega ” → 0.059±0.002 nA/ \\Omega", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_2|14", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "Page 7, line 1: “Figure 1e” → “Figure 1f”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_2|15", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "Throughout: use “×” instead of asterisk for multiplication. For example, “p*∂d” → “p×∂d”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "Single cell measurements were conducted by suspending 1000 of cells/cm3 on an OECT array assuming that a single cell would settle down on one channel. How do the authors confirm that what they detect is from a single cell?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "Figure 1e, although the current amplitude increased with the OECT configuration, relative normalized responses calculated from NR=(I_1-0)/I_0 are identical for microelectrode and OECT configuration (0.2%). Then, how do the authors claim that the sensitivity improved for OECT configuration? The advantage of OECTs over microelectrodes should be the low noise level. However, the noise level of the current measured from both devices are also similar. What could be the reason?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "How do the authors eliminate the effect of the cantilever on the current output during the electrical measurements?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "How do the authors determine the optimum frequency (1.17 kHz)? The reason why 1.17 kHz was chosen should be explained before figure 1e and 1f.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "“Qualitatively, this response is expected, as the microsphere represents a barrier for the ionic current in the electrolyte: when it is close to the sensor surface, the half-space through which ions can approach the active layer is reduced, thus increasing the effective impedance of the electrolyte Zel. Consequently, upon approach, the interfacial impedance measured with the sensor increases and the AC current amplitude drops.” The reviewer does not agree with this statement. Zel should not change for a fixed experimental system. It varies as a function of the distance between the electrodes, electrolyte conductivity, and the area of the electrodes. In addition to that, if we assume that the characteristic length, the distance between the electrode and OECT channel, is getting smaller and Zel should decrease. Moreover, interfacial impedance should not change as a function of electrolyte resistance. It can only alter with charge and ion redistribution.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "The proportionality constant (p) should be universal and does not change as a function of frequency or transistor or microelectrode parameters. Since the authors use different sizes of OECT, universality should be supported by experimental data.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_3|7", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "“Accordingly, the sensitivity is given by the slope of the approach curves shown in Figure 1e.” this should be figure 1f?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_3|8", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "The IV characteristics of three devices with different channel dimensions should be given in SI instead of normalized versions.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_3|9", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "In figure 2d, why do the sensitivity curves (for 100x100 and 50x50) of two different channels overlap each other at high frequency? It conflicts with the explanation given below.\n\n“The plot of the current amplitude versus frequency for OECTs with different channel sizes clearly shows that with increasing channel area and length a strong reduction in fc is observed.” “It is important to highlight that the position of sOECTmax corresponds to the device cutoff frequency fc (see Supp. Inf. S3 for the full mathematical treatment), and hence is a geometry-dependent parameter.” In the low-frequency regime, is the channel length dominant parameter and hence shows higher sensitivity while electrode area becomes more dominant at the high frequency?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_3|10", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "Why was the 200x50 device geometry selected for the OECT and microelectrode comparison? How does the sensitivity change for the different dimensions of microelectrodes? Moreover, the ratio of sensitivities of OECT and microelectrode seems to be higher for 50x50 channel than other channels. Why do authors move forward with 200x50 channel dimensions for the single cell measurements?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|81|Human_3|11", "source": "prb", "split": "test", "paper_id": "prb81", "comment": "The common terminology is the electrolyte gated transistor, not water gated transistors although water can also be used as the dielectric (despite with lower efficiency).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|83|Claude|1", "source": "prb", "split": "test", "paper_id": "prb83", "comment": "The paper claims to enable \"long-term stable monitoring of blood pulse signals\" but only demonstrates 7 seconds of PPG measurement with the ultraflexible device, which does not substantiate the long-term monitoring capability.\n\n\"Such self-powered, ultraflexible PPG sensors can perform long-term stable monitoring of blood pulse signals on human hands.\"\nThis claim appears in the abstract and introduction, positioning long-term monitoring as a key contribution of this work. However, the experimental demonstration does not provide evidence commensurate with this claim. Long-term monitoring in wearable health devices typically implies continuous operation over hours to days, not seconds.\n\"Such self-powered, ultraflexible PPG sensor shows a blood pulse monitoring during 7 s and can detect blood pulse rate of 77 beats per minute (bpm) on human hands.\"\nThe actual ultraflexible PPG demonstration is limited to only 7 seconds of measurement, as explicitly stated. In contrast, even the glass-substrate device was only demonstrated for 20 seconds (Fig. 4b). This 7-second window is insufficient to validate \"long-term stable monitoring\" claims, as it captures fewer than 10 heartbeats and provides no information about signal stability over extended periods.\n\"Yokota et al (2016) used a passivation layer consisting of SiON and Parylene in their photonic sensor that showed stable operation for up to 4 d. This duration is still very low compared to inorganic PPG sensors.\" from [The 2023 wearable photoplethysmography roadmap](https://iopscience.iop.org/article/10.1088/1361-6579/acead2) [[1]](#citation-list)\nThe 2023 PPG roadmap, a comprehensive review of the field, explicitly states that even 4 days of stable operation (achieved with multi-layer SiON/Parylene passivation) is \"still very low compared to inorganic PPG sensors.\" The current paper's ultraflexible PLED has a T70 lifetime of only 11.3 hours, which is substantially shorter than 4 days, making the \"long-term monitoring\" claim even less justified by field standards.\n\nReferences:\n[1] [Charlton, P.H. et al. \"The 2023 wearable photoplethysmography roadmap.\" *Physiological Measurement* **44**, 111001 (2023)](https://iopscience.iop.org/article/10.1088/1361-6579/acead2)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|83|Claude|3", "source": "prb", "split": "test", "paper_id": "prb83", "comment": "The paper acknowledges that the ultraflexible PPG sensor has significantly degraded signal quality compared to the glass-substrate device, but provides no quantitative metrics (e.g., signal-to-noise ratio) to characterize this degradation, limiting the ability to assess practical utility.\n\n\"Although the periodic signal of the OPD was visible in the result, a large noise in the detected signal was also observed.\"\nThe paper explicitly acknowledges substantial noise in the ultraflexible device's output. However, no quantitative measure of signal quality degradation is provided. Standard PPG signal quality metrics such as signal-to-noise ratio (SNR), mean absolute error in heart rate estimation, or signal quality index are not reported.\n\"Some of the reasons for the high noise in the ultraflexible PPG sensor were the large leak current of the ultraflexible OPD and the weak light intensity of the ultraflexible PLED due to the limited power supply from the ultraflexible OPV module.\"\nWhile the paper identifies potential causes for the noise, it does not quantify the magnitude of the issue or compare the signal quality metrics between glass and ultraflexible devices. Without quantitative comparison, readers cannot assess whether the ultraflexible sensor achieves clinically or practically acceptable signal quality.\n\"The reason of poor signal quality with ultraflexible PPG sensors might be the dark current increase of ultraflexible OPDs.\"\nThis further admission of \"poor signal quality\" is concerning for a device intended for health monitoring. Standard practice in PPG sensor development includes reporting SNR values, which are critical for assessing reliability. For instance, validation studies typically report MAE (mean absolute error) for heart rate estimation, as done in motion artifact reduction studies [[3]](#citation-list), but such metrics are absent here.\n\nReferences:\n[3] [Baudin, F. et al. \"Reduction of motion artifacts from photoplethysmography signals using generative adversarial networks.\" *Physiological Measurement* **46**, 015007 (2025)](https://iopscience.iop.org/article/10.1088/1361-6579/ae35cb)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|83|Claude|4", "source": "prb", "split": "test", "paper_id": "prb83", "comment": "The paper presents device performance data without error bars, statistical analysis, or information about sample sizes and device-to-device variation, which undermines the reproducibility and reliability of the reported results.\n\n\"The inverted PLED on the glass substrate showed lifetime for 70% of initial luminance as 14.7 h. In the inverted PLED encapsulated with a 1-µm-thick parylene layer, the air-operation stability of the PLED improved to 33.4 h. When the PLED was fabricated on the ultraflexible substrate, the lifetime for 70% of its initial luminance decreased to 11.3 h.\"\nLifetime values are reported as single numbers without any indication of measurement uncertainty, standard deviation, or the number of devices tested. Organic device fabrication is known to have significant batch-to-batch and device-to-device variation, making statistical characterization essential for meaningful lifetime claims.\n\"The ultraflexible PLED exhibits a current efficiency of 14 cd A⁻¹ at a current density of 24 mA cm⁻²; this efficiency is comparable to or even higher than that of the PLED on the glass substrate.\"\nEfficiency comparisons are made without error bars or statistical testing. Standard practice in OLED/PLED research includes reporting device statistics, as exemplified by recent publications that explicitly show error bars and state sample sizes (e.g., \"eight out of ten samples fall within the error range\" [[4]](#citation-list)).\n* Quote from Figure 2 caption: \"Air operational stability of the PLED under constant-current operation in ambient air.\"\nFigure 2f shows lifetime curves for three conditions (glass without passivation, glass with parylene, ultraflexible with parylene) but presents only single curves for each condition. Without replication data or error ranges, it is impossible to determine whether observed differences are statistically significant or within normal device-to-device variation.\n\nReferences:\n[4] [Hwang, J.H. et al. \"Intrinsically stretchable OLEDs with a designed morphology.\" *npj Flexible Electronics* **8**, 28 (2024)](https://www.nature.com/articles/s41528-024-00332-0)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|83|Claude|5", "source": "prb", "split": "test", "paper_id": "prb83", "comment": "The self-powered PPG system was demonstrated exclusively under 1-sun simulated sunlight conditions, while real-world indoor light operation was only theoretically calculated rather than experimentally verified, limiting the practical relevance of the self-powered claim.\n\n\"The PLED was powered by an OPV module with 10 series connections, and the OPV module was illuminated with simulated sunlight of one-sun intensity.\"\nAll experimental demonstrations of self-powered operation use idealized 1-sun (100 mW/cm²) simulated sunlight, which represents outdoor conditions on a bright, clear day. This does not represent typical usage scenarios for wearable health monitoring devices, which are often used indoors.\n\"The PCE of OPV under indoor light shows 28.1% with 1000 lux of fluorescent lamp illumination [53]. This value is equivalent as power output of 78.2 µW/cm² whereas power output under 5000 µW/cm² simulated sunlight is 290 µW/cm². With these results, our self-powered PPG system should work under 1000 lux of indoor light with OPV modules of 4.5 cm² device area.\"\nIndoor light operation is presented only as a calculation citing external literature, not as experimental demonstration. The statement \"should work\" indicates this is a prediction rather than validated performance. The required 4.5 cm² device area for indoor operation is also larger than the demonstrated system, raising questions about practical implementation.\n\"Moreover, there will be a certain challenge in the external circuit to process signal during the measurement and to monitor the signal continuously for the long-term measurement.\"\nThe paper acknowledges that continuous long-term operation faces \"certain challenges\" in external circuitry, but these are not addressed experimentally. This limitation, combined with the lack of real-world lighting validation, significantly constrains the practical applicability of the self-powered claim.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|83|GPT|1", "source": "prb", "split": "test", "paper_id": "prb83", "comment": "This paper’s core air-stability contribution (Validity; Conclusions) is not credibly supported because the manuscript gives conflicting descriptions of whether the ultraflexible PLED is unencapsulated/unpassivated, particularly between the abstract/introduction claims of “without external encapsulation” and “no passivation” and Figure 2’s caption explicitly describing “parylene encapsulation” for the ultraflexible device.\n\n\"By adopting an inverted structure and a polyethylenimine ethoxylated layer doped with 8-hydroxyquinolinato-lithium as the electron-transport layer, PLEDs exhibit improved operational stability under ambient air conditions without external encapsulation. Ultraflexible PLEDs with no passivation retain 70% of the initial luminance lifetime of 11.3\u001fh under ambient air.\" \nThese sentences are the paper’s central experimental claim: that the stability improvement occurs in ambient air without encapsulation and with “no passivation.” Because ambient oxygen/moisture ingress is a dominant failure mode in OLED/PLED systems, the encapsulation condition is not a minor detail but a defining boundary condition of the result. The lifetime number (11.3 h to 70%) is presented as a headline metric that directly substantiates the claimed breakthrough. If the devices were in fact protected by any barrier coating during the lifetime test, the abstract overstates the achievement and changes what mechanism is plausibly responsible for the stability. This inconsistency therefore weakens both the validity of the stability evidence and the reliability of the conclusions drawn from it. A precise and consistent definition of what the authors count as “passivation” versus “encapsulation” is necessary for this claim to be interpretable.\n\"f, Air operational stability of the PLED under constant-current operation in ambient air. Current density to drive PLED was set to be 8 mA/cm2. The black line indicates the PLED on the glass substrate without any encapsulation; the red line indicates the PLED on the glass substrate with parylene encapsulation; and the blue line indicates the PLED on the ultraflexible substrate with parylene encapsulation.\" \nThis figure caption directly states that the ultraflexible-substrate measurement (“blue line”) used “parylene encapsulation,” contradicting the abstract’s “without external encapsulation” and “no passivation” framing for the ultraflexible device. The caption also treats parylene as an encapsulation variable (glass without vs. glass with parylene), reinforcing that parylene is being used as a protective barrier in the authors’ own experimental design. Without clarification, readers cannot tell whether the reported 11.3 h / 70% lifetime is an intrinsic materials/architecture improvement or an encapsulation-enabled result. This matters because the paper’s motivation claims air instability prevents system integration; if parylene is required, the integration obstacle is only partially addressed. The inconsistency also makes cross-condition comparisons in Fig. 2 potentially misleading, since “ultraflexible” and “unencapsulated” are not aligned across curves. Resolving this conflict is essential before the air-stability claims can be accepted as stated.\n\"Organic Light-Emitting diodes (OLEDs) are extremely sensitive to water vapour and oxygen, which causes rapid degradation.\" [[1]](#ref1)\nThis sentence summarizes a widely recognized constraint in OLED/PLED engineering: ambient moisture and oxygen rapidly degrade device performance. Because of this sensitivity, claims of stable ambient-air operation typically hinge on carefully specified encapsulation/barrier strategies and test conditions. When the reviewed paper claims “no passivation” while a main figure caption simultaneously reports “parylene encapsulation,” the result becomes hard to interpret relative to the established degradation mechanisms. The contradiction is significant precisely because the paper positions air stability as the main obstacle to wearable integration; if stability depends on an encapsulation layer, the work’s novelty and conclusions need to be reframed accordingly. In other words, the internal inconsistency makes it unclear whether the paper demonstrates an air-stable device architecture or an air-stable packaged device. Given the field context, that distinction is critical for assessing validity and practical impact.\n\nReferences:\n[1] Grover, R. et al. “New Organic Thin-Film Encapsulation for Organic Light Emitting Diodes.” *Journal of Encapsulation and Adsorption Sciences* (2011). https://pdfs.semanticscholar.org/6fe8/8566adf91a2099f51c491a9af2a39c2efcd7.pdf", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|83|GPT|2", "source": "prb", "split": "test", "paper_id": "prb83", "comment": "The manuscript’s system-level conclusion (Conclusions; Validity) that the platform is “self-powered” and enables “long-term stable monitoring” on human hands is not robust, because the demonstrated measurement setup depends on external laboratory infrastructure (solar simulator illumination and oscilloscope readout) and does not establish autonomous operation under realistic ambient conditions.\n\n\"Long-term biological signal monitoring also requires the integration of organic optical devices with an energy harvesting power sources which does not require recharging; to make devices self-powered.\" \nThis statement defines “self-powered” in terms of eliminating recharging, implicitly setting the expectation that the presented system operates from harvested energy in typical use conditions. That expectation is strengthened by the paper’s positioning of the work as a wearable platform for monitoring on human hands. However, the manuscript does not operationalize this definition with a quantified power budget, duty cycle, or demonstration under realistic illumination environments (e.g., indoor light or unconstrained outdoor conditions). Without such evidence, the claim functions more as a conceptual motivation than a verified system property. In wearable energy-harvesting research, “self-powered” claims generally require showing that the harvester can sustain sensing, readout, and any necessary computation/communication without tethered equipment. As shown by the additional evidence below, the experimental setup relies on external instruments, which weakens the validity of the “self-powered” conclusion. Consequently, the paper does not adequately support its own criterion for “self-powered” long-term monitoring.\n\"The PLEDs were powered by ultraflexible OPV modules, and PPG data obtained from the OPD was transferred to the oscilloscope.\" \nThis sentence indicates that the signal readout path is not integrated into a wearable, autonomous device but instead depends on an oscilloscope for acquisition. An oscilloscope is a benchtop instrument that supplies measurement infrastructure (high-impedance input, sampling, storage, and often signal conditioning) that a wearable system would otherwise need to implement in an embedded form. Because the paper’s conclusion is about a system that performs “continuous” monitoring on the body, reliance on an external oscilloscope materially changes what is being demonstrated. It also leaves open whether the sensor output is sufficiently stable and power-efficient when interfaced with practical wearable electronics (e.g., a low-power ADC, microcontroller, or wireless transmitter). In short, the evidence supports that the authors demonstrated a powered optical sensor element, not a fully self-powered wearable monitoring system. This gap affects the robustness of the system-level conclusions rather than just the presentation details. As a result, the “self-powered” claim is not yet demonstrated at the system level.\n\"The PLED was powered by 10 series-connected organic photovoltaic (OPV) modules with one-sun illumination from a solar simulator.\" \nThis figure-caption sentence shows that the device is operated under one-sun illumination delivered by a solar simulator, which is a controlled laboratory source rather than a naturally occurring or everyday ambient environment. Many wearable use cases occur indoors or under variable shading and angle conditions, where OPV output can be orders of magnitude lower than one-sun and where regulation/storage become central to sustaining operation. The paper does not show whether the system works under realistic light levels, nor does it report the harvested power margin relative to the load imposed by the PLED drive and OPD readout. Furthermore, requiring “10 series-connected” OPV modules suggests that the voltage/current requirements may be high, again raising questions about practical operation in typical wearable contexts. Without experiments under relevant illumination distributions (e.g., indoor lux levels) or a power-management demonstration, the conclusions about “self-powered” continuous monitoring are not well supported. This limitation is substantial because the paper claims that energy harvesting integration is the key enabler for long-term monitoring. Therefore, the experimental evidence does not yet match the stated system-level claim.\n\"Self-powered technology means that the device can maintain its own operation by collecting energy in the working environment without an external energy supply.\" [[3]](#ref3)\nThis definition makes clear that “self-powered” is not merely about having an energy harvester present, but about sustaining operation from energy available in the intended working environment. In the reviewed paper, the demonstrated operation depends on a solar simulator to supply a standardized high irradiance and on an oscilloscope to record signals, both of which function as external infrastructure. That mismatch means the manuscript has not yet shown that the device maintains operation without external support beyond what would exist in real deployment. A convincing alignment with this definition would require at least a measured energy balance under deployment-relevant illumination and a practical, embedded readout pathway, even if minimal. Because the paper claims “continuous” biosignal monitoring, these constraints are central, not peripheral. The cited definition thus highlights that the current demonstrations fall short of a community-standard interpretation of self-powered wearable systems. Accordingly, the paper’s system-level conclusions should be weakened or better substantiated.\n\nReferences:\n[3] Xu, C. et al. “Portable and wearable self-powered systems based on emerging energy harvesting technology.” *Microsystems & Nanoengineering* (2021). https://www.nature.com/articles/s41378-021-00248-z", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|83|GPT|3", "source": "prb", "split": "test", "paper_id": "prb83", "comment": "The paper’s interpretation of air-operation stability (Conclusions; Data and methodology; Appropriate use of statistics) is not robust because key lifetime metrics (e.g., “70% lifetime,” “half of initial luminance”) are not standardized, are used inconsistently across the manuscript, and are reported without the essential contextual parameters (initial luminance, device count/variation) needed to compare against prior work.\n\n\"Ultraflexible PLEDs with no passivation retain 70% of the initial luminance lifetime of 11.3\u001fh under ambient air.\" \nThis sentence reports a “70% of the initial luminance” lifetime but does not define the test’s initial luminance, measurement geometry, or the criterion used to define the 11.3 h point beyond the 70% threshold. In OLED/PLED lifetime reporting, operational lifetime is highly dependent on initial luminance and driving conditions, so omitting these makes the number difficult to interpret or compare. The manuscript also does not state whether 11.3 h is a representative device, a best case, or an average over multiple devices, nor does it provide uncertainty or device-to-device spread. Because the paper argues that stability is the critical obstacle to system integration, this number is central to the paper’s conclusions and should be fully specified. The lack of standard lifetime notation (e.g., LT50, LT70 with defined initial luminance) weakens the robustness of the conclusions derived from the value. This is not merely a reporting style issue; it limits the scientific comparability and reproducibility of the central stability result. As a consequence, the paper’s stability claims are not methodologically transparent enough to support the strength of its conclusions.\n\"For the air-operation stability, 10\u001fwt% and 30\u001fwt% of Liq show longer lifetime to be half of initial luminance (Supplementary Fig.\u001f3d).\" \nHere the paper switches to a different lifetime criterion (“half of initial luminance,” i.e., an LT50-like metric) without reconciling it with the abstract’s “70% lifetime” metric. Using multiple lifetime thresholds is acceptable, but doing so requires explicit definitions and consistent reporting so readers understand which metric supports which claim. In its current form, the manuscript leaves ambiguity about whether the key lifetime improvement is based on LT50, LT70, or another threshold, and whether the reported 11.3 h corresponds to the same driving/initial conditions used in Supplementary Fig. 3d. This ambiguity matters because the magnitude of improvement (e.g., “more than three times”) can change depending on the chosen lifetime definition. It also prevents fair comparison to prior work, which often reports LT50 at a specified initial luminance. Because stability is the primary obstacle identified by the authors, lifetime-metric inconsistency directly affects the strength and reliability of the paper’s conclusions. Therefore, the manuscript’s stability interpretation is not currently rigorous enough.\n\"Here, we define the operational lifetime LT50 as the time for the luminance to decay to 50% of the initial luminance of 1,000 cd m\u0002 (see Supplementary Section\u001f5).\" [[2]](#ref2)\nThis sentence exemplifies a common practice in the OLED literature: operational lifetime is reported as LT50 with a specified initial luminance (here, 1,000 cd m\u0002), which anchors the metric for comparability. In contrast, the reviewed paper reports a “70% lifetime” value without stating the initial luminance used for that lifetime test in the main text. Without an initial luminance anchor, readers cannot judge whether the reported 11.3 h corresponds to a demanding brightness level or a low-brightness condition that naturally yields longer apparent lifetimes. The cited definition also shows that lifetime metrics are typically named and defined explicitly, which helps avoid confusion between LT50, LT70, and other thresholds. Because the reviewed paper’s main novelty depends on air-operation stability, it should match this level of metric specificity to support reliable interpretation. The mismatch indicates that the stability reporting falls short of common methodological standards for lifetime reporting in the field. As a result, the conclusions about stability improvement are less robust than they appear.\n\"Initial value of PLED luminance was 2153 cd/m2 with the angle of 0o.\" \nThis supplementary caption shows that the authors do sometimes record and report an initial luminance value, indicating they recognize its importance for device characterization. However, this initial luminance is reported in the context of angular distribution at 6 V, not in the context of the ambient-air lifetime tests that underpin the headline stability claims. The manuscript does not clearly connect the initial luminance during lifetime testing to the lifetime metrics reported (70% at 11.3 h, or “half of initial luminance” in Supplementary Fig. 3d). That disconnect prevents the reader from evaluating whether the lifetime was measured at a consistent brightness across device variants and comparisons. It also complicates comparison to other literature reports that normalize lifetime to specific initial luminance targets. Since the paper’s primary claim is stability enhancement for wearable integration, the lifetime test parameters must be stated with the same clarity as other characterization parameters. The evidence thus supports that key stability metrics are currently under-specified.\n\nReferences:\n[2] Fukagawa, H. et al. “Operational lifetimes of organic light-emitting diodes dominated by Förster resonance energy transfer.” *Scientific Reports* (2017). https://pmc.ncbi.nlm.nih.gov/articles/PMC5431848/", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|83|GPT|4", "source": "prb", "split": "test", "paper_id": "prb83", "comment": "The manuscript’s conclusion that the device enables meaningful continuous biosignal monitoring (Validity; Conclusions) is insufficiently supported because the PPG demonstration is extremely short, lacks validation against a reference standard (e.g., ECG or a clinical-grade PPG), and does not provide quantitative accuracy/agreement metrics.\n\n\"Such self-powered, ultraflexible PPG sensor shows a blood pulse monitoring during 7\u001fs and can detect blood pulse rate of 77 beats per minute (bpm) on human hands.\" \nThis sentence describes the entirety of the on-body biosignal evidence as a 7-second recording yielding a single heart-rate value (77 bpm). A 7-second trace is insufficient to demonstrate “continuous” monitoring, stability over time, or robustness to common wearable confounders such as motion artifacts, contact variability, and ambient light changes. The paper also does not provide information about repeated trials, subject count, or intra/inter-subject variability, all of which are necessary to interpret whether the signal quality is reproducible. Moreover, reporting one bpm value without uncertainty or error bounds does not establish measurement accuracy. Because the manuscript positions biosignal monitoring as the target application and uses this demonstration to support system-level claims, the extremely limited scope materially weakens the validity of the conclusions. In typical wearable biosensing work, authors provide longer recordings and quantitative agreement to a reference to justify monitoring claims. Therefore, this evidence is not sufficient to substantiate the strength of the biosignal claims.\n\"The PLED was powered by 10 series-connected organic photovoltaic (OPV) modules with one-sun illumination from a solar simulator.\" \nThis caption detail indicates that the PPG measurement is demonstrated under a controlled, high-irradiance laboratory illumination condition rather than under realistic ambient lighting. In practice, PPG signal quality is sensitive to the stability of the light source, photodetector operating point, and environmental light interference, all of which can change under real-world illumination. Demonstrating PPG under a solar simulator does not address whether the system remains functional under indoor light, variable outdoor light, or partial shading typical for on-body use. The caption also does not mention any reference measurement for heart rate, so the reader cannot assess whether the observed waveform corresponds accurately to physiological pulse timing. Because this setup is central to the paper’s claim of self-powered biosensing, the lack of realism and validation limits what can be concluded from the demonstration. The methodological gap is consequential for the paper’s claimed application rather than a minor experimental choice. As a result, the PPG evidence does not robustly support the “continuous monitoring” conclusion.\n\"The comparison of the quality-filtered in-ear heart rate data with the reference ECG resulted in a bias of 0.78 bpm with a standard deviation of \u001f\u001f2.54 bpm; Pearson\u001fs Correlation Coefficient PCC = 0.83; Intraclass Correlation Coefficient ICC = 0.81 and mean absolute percentage error MAPE = 2.57.\" [[4]](#ref4)\nThis sentence illustrates common validation practice in wearable PPG research: heart-rate estimates are compared to a reference ECG and summarized with quantitative agreement metrics such as bias, standard deviation, and correlation. The reviewed paper does not provide any analogous reference comparison, so it cannot claim that the measured pulse rate is accurate rather than merely plausible. It also provides no uncertainty or statistical characterization of measurement error, which is necessary for interpreting a biosensor’s utility. While the reviewed paper’s primary novelty may be materials/system integration, it explicitly claims functional biosignal monitoring on the body, which requires at least minimal validation against a standard. The cited example also shows that robust validation often involves large datasets and extended recordings, emphasizing how underpowered a 7-second demonstration is for drawing conclusions about monitoring capability. Thus, relative to established practice, the reviewed paper’s biosignal evidence is not sufficient to support its system-level conclusions. This deficiency affects the validity of the claimed application.\n\"Supplementary Figure 18 | Long-term measurement of PPG systems on ultraflexible substrate. Ultraflexible PLED was powered by ultraflexible OPV module. the voltage was obtained from ultraflexible OPD with the PLED illumination. All devices were used with the supporting glass substrate.\" \nThis supplementary caption indicates that a “long-term measurement” was performed using a supporting glass substrate, which differs from the manuscript’s emphasis on ultraflexible, skin-conformal operation. Using a supporting glass substrate can meaningfully change mechanical conformity and optical coupling conditions, both of which can affect PPG signal quality and stability. The caption also describes voltage acquisition but does not report any quantitative performance metrics (duration, drift, signal-to-noise ratio, or accuracy against a reference). Consequently, it does not resolve the central gap that the paper lacks validated, quantified evidence of biosignal monitoring quality over time. Moreover, juxtaposed with the paper’s on-hand 7-second claim, it suggests that the “long-term” aspect may have been evaluated under mechanically supported conditions rather than true wearable conformal use. This reduces the strength of conclusions about continuous monitoring “on human hands.” The evidence therefore supports that the biosignal claims are not yet adequately substantiated.\n\nReferences:\n[4] Adams, T. et al. “Accurate detection of heart rate using in-ear photoplethysmography in a clinical setting.” *Frontiers in Digital Health* (2022). https://www.frontiersin.org/journals/digital-health/articles/10.3389/fdgth.2022.909519/full", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|83|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb83", "comment": "The paper claims the device is \"ultraflexible\" but fails to demonstrate sufficient mechanical durability compared to established standards in the field.\n\n\"In the cyclic bending test, the ultraflexible PLED was bent cyclically to the bending radius of 5 mm. The results of the bending test is shown in Supplementary Fig. 8. Even after the device was bent cyclically with 50 times, the J-V curves did not show any degradation\"\nThe bending test parameters (50 cycles at 5 mm radius) are significantly less rigorous than the state-of-the-art for \"ultraflexible\" electronics. A radius of 5 mm is relatively large compared to the micrometer-scale flexibility typically demonstrated for such devices, and 50 cycles is insufficient to prove long-term mechanical stability, which usually requires thousands of cycles.\n\"Our passivation layer extended the operational half-life (with regard to luminance) from 2 to 29 hours. More detailed characteristics of the PLEDs... The device characteristics were invariant after 1000 cycles of bending at a radius of 100 μm\" [1]\nThis reference (Yokota et al., 2016), which is also cited in the paper as [28], demonstrates mechanical stability over 1000 cycles at a much smaller bending radius of 100 μm. The current paper's test (50 cycles at 5 mm) falls far short of this established benchmark, undermining the claim of \"ultraflexible\" durability.\n\"We demonstrate ultraflexible and conformable three-color, highly efficient polymer light-emitting diodes (PLEDs)... withstand repeated bending (radius 5 μm)\" [2]\nThis reference (Kaltenbrunner et al., 2013), cited as [24], also demonstrates flexibility at a much smaller radius (5 μm) than the 5 mm used in this paper. The lack of comparable testing makes the \"ultraflexible\" claim weak.\n\nReferences:\n[1] Yokota, T. et al. \"Ultraflexible organic photonic skin.\" *Sci. Adv.* **2**, e1501856 (2016). https://www.science.org/doi/10.1126/sciadv.1501856\n[2] Kaltenbrunner, M. et al. \"An ultra-lightweight design for imperceptible plastic electronics.\" *Nature* **499**, 458–463 (2013). https://www.nature.com/articles/nature12314", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|83|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb83", "comment": "The paper claims \"continuous bio-signal detection\" but the device only operates under illumination, failing to address the requirement for operation in dark or low-light conditions which is essential for continuous monitoring.\n\n\"The PLED switched on when the OPV module was exposed to the sunlight, and it switched off when the OPV module was stored in the dark.\"\nThis explicitly states that the device stops working in the dark. \"Continuous\" monitoring implies operation 24/7 or at least during sleep and other activities where light might not be available. The reliance on direct illumination for power contradicts the \"continuous\" claim.\n\"Another critical requirement for self-powered device is the auxiliary battery, especially for their stable operation in dark situation. In Supplementary Fig. 20, the circuit with auxiliary rechargeable battery are explained.\"\nThe authors acknowledge the need for a battery for dark operation but do not integrate it into the main demonstrated system or provide performance data for the battery-assisted mode in the main text. The primary claim of \"self-powered... for continuous bio-signal detection\" is thus misleading as the self-powered aspect (energy harvesting) is insufficient for continuous operation without an external storage component that is not fully characterized in the main results.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|83|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb83", "comment": "The paper claims the system \"should work\" under indoor light based on calculations but fails to experimentally demonstrate this, despite \"self-powered\" being a key feature.\n\n\"With these results, our self-powered PPG system should work under 1000 lux of indoor light with OPV modules of 4.5 cm² device area.\"\nThis claim is speculative (\"should work\") and relies on a calculation rather than experimental verification. Given the significant difference in power density between the tested condition (5000 µW/cm², approx. 0.05 sun) and indoor light (approx. 100-500 µW/cm² depending on spectrum), experimental proof is necessary to validate this claim.\n\"The PLED was observed to emit bright light with an input light intensity of about 5000 µW/cm², which is 0.05 times the intensity of sunlight\"\nThe demonstrated operation required 5000 µW/cm², which is significantly higher than typical indoor lighting (1000 lux is roughly 1-2 W/m² or 100-200 µW/cm² for many sources, though the paper cites a specific conversion). The gap between the tested intensity and the claimed indoor capability is large, and without a demonstration at 1000 lux, the claim is unsupported.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|83|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb83", "comment": "The reported PPG signals from the ultraflexible sensor show \"large noise\" and \"poor signal quality\", raising concerns about the reliability and accuracy of the bio-signal detection which is the paper's primary application.\n\n\"Although the periodic signal of the OPD was visible in the result, a large noise in the detected signal was also observed. Some of the reasons for the high noise in the ultraflexible PPG sensor were the large leak current of the ultraflexible OPD and the weak light intensity of the ultraflexible PLED\"\nThe authors admit to \"large noise\" and \"poor signal quality\". For a paper focused on \"bio-signal detection\", the quality of the signal is paramount. High noise levels can lead to inaccurate heart rate calculations (e.g., the reported 77 bpm) and artifacts.\n\"The reason of poor signal quality with ultraflexible PPG sensors might be the dark current increase of ultraflexible OPDs... which would leads high dark current of OPD and poor signal quality of PPG.\"\nThe paper identifies the cause (dark current) but does not solve it or provide a quantitative analysis of the signal-to-noise ratio (SNR) or error rate compared to a reference device. Without such analysis, the reliability of the \"continuous bio-signal detection\" is questionable.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|83|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb83", "comment": "Regarding the poor quality of the PPG signal, the authors attributed it to the dark current increase of the OPD due to the rigidity and roughness of the ZnO layer used in the inverted structure. However, the OPD they fabricated is already ultraflexible, and the rigidity of a single layer shouldn't be a concern. The authors should further clarify the actual reason for the poor signal quality.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|83|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb83", "comment": "The author should specify the light intensity used to measure the rise and fall time of the OPD. The response speed of the organic photodetector may drop significantly at low light intensity.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|83|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb83", "comment": "The major problem is the non-diode behavior of the device in Fig. 2c, it doesn't show a turn-on, hence, it's not a light-emitting \"diode\". While the authors explained the ZnO layer surface roughness is the culprit. It will be good to provide the same characterization for the glass device to convince readers that ZnO is problematic in the ultra-flexible device, while it is not for the glass device.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|83|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb83", "comment": "Connecting solar cells to LEDs without power regulation and storage will create a variable drive current in the LEDs, that will change your current output from the OPD. Therefore, the bio-signal will be unreliable. Please ensure this is stated in the caption of the figure as well as the manuscript.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Claude|1", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "The paper claims that the soft robots enable \"long-term operation\" as implants, but the in vivo biocompatibility studies are limited to only 14 days, which is insufficient to assess chronic biocompatibility, fibrotic encapsulation, or long-term device stability for the proposed clinical applications.\n\n\"Additionally, histological analysis reveals that the soft robots implanted inside chest chamber of mice induce no observable inflammation or other adverse effects to surrounding tissues, indicating good biocompatibility for long-term operation (Fig. S55 & Fig. S56).\"\nThe paper claims \"good biocompatibility for long-term operation\" based on histological analysis. However, examining Fig. S56 in the supplementary materials reveals that the histological assessment was only conducted at Day 1, Day 3, Day 7, and Day 14. A 14-day study is generally considered a short-term or acute assessment in the implant biocompatibility field, insufficient to evaluate chronic responses such as fibrous capsule formation, chronic inflammation, or tissue integration that typically develop over weeks to months. For devices intended for long-term implantation, FDA and ISO standards typically require evaluation periods of at least 4-12 weeks.\n\"Fig. S56. Histological analysis (H&E staining) of the cardiac tissue after implantation of a hydrogel-based thera-gripper. (A) Day 1. (B) Day 3. (C) Day 7. (D) Day 14. (H&E staining, N=3). Scale bars, 100μm.\"\nThe study uses only N=3 samples per timepoint and extends only to 14 days. This is inadequate to characterize chronic tissue responses. According to established biocompatibility testing standards for implantable devices, longer implantation periods (typically 30+ days) are required to observe the full spectrum of host responses including foreign body reaction, which typically peaks at 2-4 weeks and transitions to chronic inflammation thereafter. The small sample size also limits statistical power for detecting adverse effects.\n\"PNIPAM and PNIPAM co-3 % APTA hydrogels are biocompatible in a female and male murine model over a 30-day period, maintaining stable hematological, biochemical, and histological parameters without alterations.\" [[1]](#citation-list)\nRecent literature on PNIPAM biocompatibility, such as this 2025 study, demonstrates that even minimum biocompatibility assessments for PNIPAM hydrogels require at least 30-day implantation periods to establish baseline safety. The 14-day assessment in the reviewed paper falls short of this minimum standard, making the claim of suitability for \"long-term operation\" insufficiently supported.\n\nReferences:\n[1] [In vivo biocompatibility of poly-N-isopropylacrylamide (PNIPAM) hydrogels in Wistar rats: Hematological, biochemical, and histopathological assessments. PubMed 2025](https://pubmed.ncbi.nlm.nih.gov/41666514/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Claude|4", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "Three of the four major applications demonstrated in the paper (bladder volume monitoring, blood pressure sensing, and ingestible gastric robot) use artificial phantom models (balloons, rubber tubes, ex vivo tissue) rather than in vivo animal models with actual physiological function, limiting the translational validity of the claimed functional capabilities.\n\n\"A balloon model was used to mimic the natural bladder to evaluate the actuation and sensing performance of the soft gripper.\"\nThe bladder volume sensing application is demonstrated exclusively using an artificial balloon model. While this provides proof-of-concept for the mechanical sensing principle, it does not validate functionality in a physiologically relevant environment. Real bladder tissue has different mechanical properties than balloons, and in vivo conditions include factors such as tissue motion, biochemical environment, and physiological filling/voiding cycles that cannot be replicated with balloon models. The claim that this system could \"enable coordinated, closed-loop operation of bladder-volume evaluation and electrical stimulation to treat overactive bladder\" requires in vivo validation.\n\"A rubbery tube was used to mimic the artery system to evaluate the performance of the soft robotic cuff. The soft robotic cuff can twist around the artificial artery upon thermal stimulation. A pulsatile flow of water was created to simulate the pulsation pattern of the artery system.\"\nSimilarly, blood pressure monitoring is demonstrated using a rubber tube with pulsatile water flow rather than an actual blood vessel. Arterial tissue has viscoelastic properties, vessel compliance varies along the arterial tree, and blood exhibits non-Newtonian fluid dynamics that differ substantially from water. The paper shows only ΔR/R strain response (Fig. 5J-K) without calibration against actual blood pressure measurements from invasive catheterization, which would be necessary to validate blood pressure monitoring claims.\n\"The fabrication of a soft ingestible robot... The PEDOT:PSS/PVA hydrogel pH sensors were adhered onto the side of Au/PI film\"\nThe ingestible robot for gastric pH monitoring and drug delivery is characterized entirely in vitro using PBS solutions at different pH values. No in vivo gastric deployment is demonstrated, despite claims that the robot can \"reside inside stomach for prolonged monitoring and drug delivery.\" The harsh gastric environment (pH 1-3, enzymatic activity, mechanical churning) presents challenges that cannot be assessed through benchtop characterization alone. Only the cardiac application includes actual in vivo animal testing.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Claude|5", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "The wireless power transfer characterization shows that power transmission efficiency degrades significantly under conditions of device deformation, misalignment, and distance increase, yet the paper does not adequately address how these limitations would affect reliable operation in dynamic in vivo environments where such variations are inevitable.\n\n\"Furthermore, We conducted computational and experimental investigations to analyze the influence of separation distances between receiving and emission coils, horizontal offsets, orientation angles on the power transfer efficiency (Fig. S31). As expected, an increase in separation distance, horizontal offset and orientation angle leads to a decrease in the power transfer efficiency.\"\nWhile the paper acknowledges that power transfer efficiency decreases with distance, offset, and angular misalignment, it does not provide specific quantitative data on the acceptable ranges for reliable actuation. Figure S31 shows efficiency drops, but the supplementary note does not clearly define the operational envelope within which sufficient power can be delivered for actuation. This is particularly important for applications like the cardiac thera-gripper, where the heart's beating motion would cause continuous changes in receiver coil position and orientation.\n\"The shape deformation including twisting, distorting, and bending are altered and the power transmitted are measured for each situation.\"\nFigure 4O in the main paper shows that output power varies significantly (from ~0.05W to ~0.9W) depending on the deformation state (normal, twisting, distorting, bending) at peak resonant frequency (~17 MHz). For applications requiring consistent actuation, these variations could result in inconsistent robotic behavior. The PNIPAM actuation requires maintaining temperatures above the LCST (34°C), and power fluctuations due to device movement could lead to unintended partial actuation or failure to actuate. The paper does not present closed-loop control strategies to compensate for these variations in a dynamic environment.\n\"In wireless power transfer applications for MIDs, the primary measure of the tissue safety is considered as the specific absorption rate (SAR). It is the unit of measurement for the amount of radio frequency energy absorbed by a body when using a wireless device.\" [[4]](#citation-list)\nThe paper does not report SAR measurements or simulations for the wireless power transfer system operating in tissue. While the thermal heater characterization addresses local heating, the RF exposure from the wireless power transmission could also contribute to tissue heating through electromagnetic absorption. Comprehensive safety assessment for implantable wireless devices typically requires SAR evaluation to ensure compliance with IEEE C95.1 standards, which is absent from this work.\n\nReferences:\n[4] [Wireless Power Transfer Techniques for Implantable Medical Devices. PMC, 2020](https://pmc.ncbi.nlm.nih.gov/articles/PMC7349694/)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|GPT|1", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "This paper’s central claims about organ-level implant utility (bladder control, vascular blood pressure monitoring, and gastric residence with drug delivery) are not supported because the reported validations rely largely on simplified in vitro models rather than experiments in the intended physiological environments.\n\nFurthermore, integration of a battery-free wireless module into these robots enables operation and communication without tethering, thus enhancing the safety and biocompatibility as minimally invasive implants. Demonstrations range from a robotic cuff encircling a blood vessel for detecting blood pressure, to a robotic gripper holding onto a bladder for tracking bladder volume, an ingestible robot residing inside stomach for pH sensing and on-site drug delivery, and a robotic patch wrapping onto a beating heart for quantifying cardiac contractility, temperature and applying cardiac pacing, highlighting the application versatilities and potentials of the nature-inspired soft robots.\nThis sentence frames multiple organ-specific “demonstrations” as evidence of minimally invasive implant capabilities across distinct physiological contexts (blood vessel, bladder, stomach, heart). However, the paper’s own descriptions of several validations show they are conducted on surrogate benchtop models (balloons, rubber tubes, PBS assays), not in living organ environments. That distinction is consequential because implant performance is governed by tissue compliance, biofouling, organ motion, and physiologic boundary conditions that are absent in these surrogates. When the manuscript uses strong application language (“detecting blood pressure,” “tracking bladder volume,” “residing inside stomach”), readers reasonably interpret these as validated in the corresponding target environment. Without organ-relevant in vivo (or at least ex vivo) validation for each core application, the breadth of claimed implant utility is not justified by the presented evidence. This directly weakens the validity of the paper’s overarching conclusion about a broadly deployable implant platform.\nWe use a balloon model to mimic the natural bladder behavior of filling and emptying to validate performance of the integrated soft robotic gripper.\nThe bladder system is explicitly validated on a balloon model, which cannot reproduce bladder wall histology, anisotropic compliance, lubrication, or the complex constraints of the pelvic environment. A balloon also sidesteps key implant issues such as durable attachment to wet tissue, motion artifacts from neighboring anatomy, and damage risks from chronic contact. Because the same section positions the system as “voiding treatment” with “wireless closed-loop control,” the balloon test cannot establish that the intervention is therapeutically effective or even safe when applied to real bladder tissue. In implantable bioelectronics and soft robotics, benchtop surrogates are commonly used for early sensor linearity checks, but they are not sufficient evidence for organ-level claims. Consequently, the paper’s interpretation that this validates a bladder implant function is not robust. The conclusions should be narrowed to prototype characterization unless organ-relevant testing is provided.\nAn in vitro model of artery that uses a rubbery tube with a pulsatile flow of water to create a simulated pulsation pattern validates performance of the soft robotic cuff (Fig. S50B & C and Fig. 5 I).\nA rubber tube with water does not replicate arterial wall biomechanics, surrounding soft tissue constraints, blood rheology, or the physiological variability that drives baseline drift and motion artifacts in implanted pressure sensors. The word “validates” overstates what such a simplified setup can demonstrate for a cuff intended to measure blood pressure on real vessels. In practice, vascular sensing claims generally require evaluation in ex vivo vessels or in vivo models to show stable coupling, calibration, and robustness under biological conditions. This setup also cannot reveal adverse effects such as ischemic constriction or vessel irritation, which are central to implant safety. Therefore, the evidence supports only benchtop feasibility, not implant-grade performance. As written, the conclusion that the cuff enables real-time blood pressure measurement as an implant is not sufficiently supported.\nFurthermore, such nature-inspired designs of soft sensory robots can also configure into an ingestible platform. Here, we show that a soft ingestible robot is capable of prolonged residence in the stomach for pH monitoring and drug delivery. Fig. S51A depicts the proposed structure of the ingestible robot based on a slab-shaped muscle layer sandwiched by two e-skin layers consisting of a drug delivery module and a pH sensing module (Fig. 5 L, more details appear in the Materials and Methods.). The miniaturized size of the robot facilitates swallowing and transport through the esophagus to stomach (Fig. 5 L). Once in the stomach, the robot self-expands that prevents passage through the pylorus for an extended duration in the gastric environment (Fig. 5 M and Fig. S51B). The soft pH sensors based on PEDOT:PSS/poly(vinyl alcohol) (PVA) embedded onto the e-skin of the robot provide continuous measurements of gastric pH (Fig. S51C and Fig. 5 N). The pH sensor exhibits a linear relationship between the resistive change and pH of the fluidic environment within the range of acidic (pH ~ 3) to basic (pH ~ 8) (Fig. S51E). To realize prolonged drug release, the integrated drug patches use poly(lactic-co-glycolic acid) (PLGA) as a matrix to load drugs and the robotic motion as a trigger mechanism that exposes the drug-loaded patches to stomach fluid for initiating drug release. As a demonstration, we use a biocompatible dye, rhodamine-B (RB), as a model drug (5 mg of RB per 0.5g PLGA). Figure 5 O and Fig. S51H show the UV-vis absorption spectra and the corresponding dosages, respectively, of the RB-loaded drug patch, immersed in PBS solution (at pH ~ 5) for 1 h under various temperatures ranging from 25°C to 45°C (Fig. S51F & G show the calibration curve based on the measured UV-vis absorption spectra.).\nThe manuscript asserts “prolonged residence in the stomach,” but the described quantitative drug-release assay is a 1-hour PBS immersion experiment with a model dye. A short benchtop immersion test cannot demonstrate gastric residence under peristalsis, mucus turnover, and clearance through the pylorus, which are exactly what “residence” depends on. Likewise, PBS at pH ~5 is a simplified medium that does not represent gastric acidity, enzymes, and food-dependent mechanical and chemical conditions that affect both sensors and polymer release. As a result, the evidence provided directly substantiates neither prolonged retention nor drug delivery under stomach conditions. This mismatch between strong residence/drug-delivery claims and limited assay conditions weakens the reliability of the ingestible-robot conclusions. At minimum, the paper would need direct retention evidence (imaging over time) and pharmacokinetic or local concentration measurements in relevant models.\nLast, the integrated bladder system is implanted in three rats for in vivo characterization, and the results demonstrate the sensor’s repeatable performance and high voiding efficiency. ([3](#ref3))\nThis related work provides a clear example of how bladder-assist and sensing-actuation claims are commonly validated: by implantation and quantitative in vivo performance in animals. The quoted sentences show that voiding efficacy and sensing repeatability are assessed under physiological conditions, which directly tests the implant-environment coupling that benchtop balloons omit. The contrast matters because the reviewed paper makes similarly application-level claims about bladder monitoring and closed-loop treatment but presents a balloon-based validation instead. This does not mean the reviewed approach is invalid, but it shows the current evidence is not at the same validation level as closely related peer-reviewed demonstrations. The comparison therefore supports the critique that the reviewed paper’s bladder-implant conclusions are premature. A more rigorous validation path (in vivo or at least ex vivo) is necessary for comparable claims.\nHere, we report that GI parasite–inspired active mechanochemical therapeutic grippers, or theragrippers, can reside within the GI tract of live animals for 24 hours by autonomously latching onto the mucosal tissue. ([4](#ref4))\nThis literature illustrates that residence claims in the GI tract are typically validated by measuring retention time in live animals, because clearance by motility is the main failure mode. The reviewed manuscript uses similarly strong language (“prolonged residence in the stomach”) but does not present analogous retention measurements, instead emphasizing PBS immersion release results. The comparison highlights that “residing” is not only a design intent but an experimentally verifiable property requiring time-resolved in vivo evidence. Without such evidence, claims of prolonged gastric residence and associated drug delivery remain speculative. This directly challenges the robustness of the reviewed paper’s ingestible-robot conclusions. Aligning claim strength to the validation depth would materially improve the paper’s credibility.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|GPT|2", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "This paper draws long-term biocompatibility and safety conclusions for implantable robots from limited short-duration assays and small-sample histology, which is insufficient to justify “long-term operation” and implant safety claims across the diverse device use-cases (thermal actuation, wireless power transfer, electrodes, and hydrogel adhesion).\n\nThe as-fabricated soft robot can form a highly conformal interface with diverse biological surfaces, indicating its inherent mechanical softness and high biocompatibility (Fig. 2 F, Fig. 2 G, and Fig. S2C-E).\nA conformal interface is an important mechanical design goal, but conformality alone does not establish biocompatibility, especially for chronically implanted devices. Biocompatibility depends on the material chemistry, leachables, mechanical wear, and the biological response over the intended exposure duration. This sentence explicitly uses interface conformality as evidence (“indicating”) of “high biocompatibility,” which is an inference not directly supported by the stated observation. In implantable-device evaluation, a conformal fit can coexist with adverse foreign body response, fibrosis, or tissue injury from thermal/electromagnetic exposure. The paper’s use of “high biocompatibility” at this stage therefore over-interprets what the cited evidence can show. Stronger evidence (endpoint-specific testing and longer follow-up) is needed to justify the conclusion.\nHere, mouse 3T3-J-2 cells exposed to complete soft robotic devices with constituent materials including pure PNIPAM hydrogel and functional nanocomposites (e.g., AgNWs, RGO, PEDOT:PSS & MXene), remain robust healthy and maintain stable viability (Fig. 6 A, Fig. 6 B, Fig. S53 & Fig. S54) [108,109]. Additionally, histological analysis reveals that the soft robots implanted inside chest chamber of mice induce no observable inflammation or other adverse effects to surrounding tissues, indicating good biocompatibility for long-term operation (Fig. S55 & Fig. S56).\nThe in vitro cell exposure and a limited in vivo implantation histology are useful screening steps, but they do not, on their own, justify a general conclusion of “long-term operation” safety for diverse implant configurations and functions. The cell study duration is short (the supplementary captions specify 48 hours), which cannot capture chronic inflammatory processes, fibrotic encapsulation, or degradation-driven toxicity. The in vivo histology is described qualitatively (“no observable inflammation”), without specifying the full endpoint set needed for the various tissue contacts and exposure modes the paper proposes. The statement also jumps from local observations in a mouse chest chamber to “long-term operation” broadly, which is a stronger claim than the evidence supports. For devices that include wireless power transfer and electrothermal actuation, safety must consider not only material toxicity but also temperature rise and electromagnetic exposure. Therefore, the conclusion is overstated relative to the duration and scope of testing shown.\nFig. S53. Cell viability assessment of soft robotic implants. (A-H) Confocal microscope images of 3T3-J-2 cells before (control) and after exposure to various functional nanocomposites, including PNIPAM hydrogel, AgNWs, RGO, PEDOT:PSS and MXene-based composites, as well as as-prepared soft robotic devices integrated with an e-skin layer and PNIPAM hydrogel-muscle layer, incubated for 48 hours.\nThis caption confirms that the main cell viability evidence is a 48-hour exposure window, which is short relative to typical “long-term” implant claims. Many clinically relevant failure modes (e.g., delamination, leachables accumulating, mechanical fatigue, and chronic immune response) manifest over weeks to months, not 48 hours. Short-term viability also does not guarantee that devices remain stable and non-toxic under repeated actuation cycles or under physiological protein adsorption and biofouling. Moreover, viability assays do not address organ-specific risks such as hemocompatibility for cardiovascular use or mucosal irritation for GI use. As a result, these data are best interpreted as preliminary screening rather than evidence supporting long-term implant biocompatibility. The manuscript should therefore temper its long-term safety claims or add longer-term, endpoint-specific evidence.\nFig. S55. Histological analysis (H&E staining) of biological tissues after thermal stimulation using a robotic implant. Histological analysis of lung tissue (A-C), heart tissue (D-F), spleen tissue (G-I), and liver tissue (J-L) after thermal stimulation at a power of 0.1 W, with durations of half an hour and one hour, respectively. (H&E staining, N=3).\nThis experiment probes acute tissue response to a specific thermal stimulation regime (0.1 W for 0.5–1 hour), but it does not establish safety across the operating envelope described elsewhere (e.g., ~1 W harvested power for actuation) or under repeated/chronic exposure. The sample size is small (N=3) and the endpoint is limited to H&E morphology, which may miss subtle immune activation, fibrosis, or functional impairment. Acute histology after short stimulation also cannot address cumulative thermal damage or immunological response to recurrent heating. For an implantable robotic platform, the intended exposure may be prolonged and intermittent over days to months, so acute tests are necessary but not sufficient. Additionally, the experiment does not explicitly connect to the device’s most demanding conditions (wireless actuation and in-tissue operation). Therefore, these data cannot support the broader conclusion of long-term safety.\nFig. S56. Histological analysis (H&E staining) of the cardiac tissue after implantation of a hydrogel-based thera-gripper. (A) Day 1. (B) Day 3. (C) Day 7. (D) Day 14. (H&E staining, N=3).\nA 14-day follow-up provides more relevant evidence than acute studies, but it remains limited for “long-term operation” claims, particularly for chronic implants where foreign body response and encapsulation can evolve over longer periods. The endpoint is still limited to H&E staining, and the sample size remains small (N=3), which limits confidence and generalizability. The caption does not indicate whether actuation, pacing, or wireless power transfer occurred chronically during the implantation period, which would be critical for assessing real-use safety. Furthermore, a thera-gripper implanted in the chest chamber does not necessarily generalize to other anatomical sites or to GI mucosal contact or vascular contact use-cases. Thus, while suggestive of short-term tolerability, these data do not justify broad long-term biocompatibility conclusions for the platform. More comprehensive, function-under-use and longer-duration evaluations would be needed.\nAn assessment of potential biocompatibility risk should include not only chemical toxicity, but also physical characteristics that might contribute to an unwanted tissue response. These characteristics can include surface properties, forces on surrounding tissue (e.g., mechanical, thermal, electromagnetic), geometry, and presence of particulates, among others. ([1](#ref1))\nFDA’s guidance explicitly notes that biocompatibility risk is not limited to chemical toxicity and that physical characteristics—including thermal and electromagnetic forces—can drive unwanted tissue responses. This is directly relevant because the reviewed platform relies on electrothermal actuation and RF wireless power transfer, both of which impose thermal and electromagnetic stresses on surrounding tissue. The manuscript does not present a structured evaluation of these risks under realistic implant conditions (e.g., tissue temperature rise maps, induced-current considerations, or failure-mode analysis). Instead, it largely extrapolates safety from short-term cell viability and limited histology, which do not address these physical-hazard mechanisms. Because thermal/electromagnetic hazards are central to the device’s mode of operation, omitting endpoint-specific evaluation weakens the validity of the safety conclusion. The paper should either provide such analyses or substantially narrow its safety claims.\nISO 10993-1 helps determine whether a device’s materials are safe for their intended use, considering both composition and exposure duration. ([5](#ref5))\nThis ISO overview statement captures a core principle of medical-device biological evaluation: exposure duration is a central determinant of what evidence is required. The reviewed paper frequently uses language consistent with long-duration implantation (e.g., “long-term operation,” “prolonged residence”), but the presented testing is mostly short-term and does not clearly match to intended exposure durations per use-case. When exposure duration changes (e.g., transient vs. long-term), the required endpoints and confidence level change substantially. Therefore, citing limited short-term tests as support for long-term claims is inconsistent with standard biocompatibility evaluation practice. This reinforces the critique that the manuscript’s long-term safety conclusions are overstated. A clearer mapping from intended use to duration-dependent evaluation would be required for robust claims.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|GPT|3", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "This paper claims the wireless power transfer and electrothermal actuation strategy is safe for implant use (minimal heat damage and reduced tissue damage/infection), but it does not present tissue-relevant dosimetry and thermal safety evidence, and its simulations use non-physiologic material assumptions.\n\nWireless operation of actuation as well as therapeutic and/or diagnostic functions is essential for implantable robots to minimize tissue damage and implant infection [67,69–71]. However, existing schemes for wireless operation of robots mostly require sophisticated circuitry for energy harvesting and storage, which may introduce non-negligible heat (~ 80°C), unfavored space occupation, system complexity, limited lifetimes, and high cost [72,73].\nThese sentences motivate the proposed wireless approach partly on safety grounds, implying reduced tissue damage/infection compared to alternatives. Yet the manuscript does not provide a direct safety comparison (e.g., temperature profiles in tissue, thermal dose, or adverse event rates) to substantiate this claim. Raising the concern of “~80°C” heat in prior schemes heightens the expectation that the current method will be evaluated against clinically relevant thermal injury thresholds. Without tissue-relevant measurements, readers cannot assess whether the proposed system truly avoids hazardous heating, especially when delivering substantial power to heaters. Moreover, implant infection risk is not solely a function of tethering; it depends on surgical approach, encapsulation, and chronic tissue response, none of which are quantitatively addressed here. Therefore, the safety rationale is not convincingly supported by corresponding evidence. This undermines validity for the safety-related conclusions.\nFigure 4 I shows an infrared image of the robotic finger highlighting concentrated heat on the electrical heater and minimum heat on the receiving inductor, which collectively ensures a stable power supply and minimum heat damage to surrounding bio-environments in potential usage as implants. Figure 4 K shows the output power as a function of frequency. The wireless power transfer system achieves the highest harvested power ~ 1.05 W at a frequency of 15 MHz.\nThe paper infers “minimum heat damage” from an infrared image and coil/heater temperature distribution, but IR thermography typically measures surface temperatures in air and does not substitute for temperature rise in perfused tissue. The harvested power level (~1.05 W at 15 MHz) is substantial for an implantable heater, and safety depends on how much heat is deposited into surrounding tissue and for how long, not merely that the receiving inductor itself is cooler. Additionally, “minimum heat damage” is a biological claim that requires either histology/function endpoints under the relevant operating conditions or a validated thermal/dosimetric model in tissue. The evidence presented here does not quantify tissue temperature rise, spatial thermal gradients in vivo, or exposure duration under closed-loop operation. Without those, the conclusion that the method avoids heat damage in “bio-environments” is not supported. This leaves a critical safety and feasibility gap for implant translation.\nThe default conductivity, permittivity, and susceptibility of the copper and air derived directly from the materials library of the software were used in the simulations.\nThis sentence indicates that the electromagnetic simulations for power transfer are performed with copper and air as the primary material environment, rather than tissue-representative dielectric and conductive properties. In implant use, surrounding media are conductive, lossy, and heterogeneous (skin, fat, muscle, blood), and these properties strongly affect coupling efficiency, induced currents, and heating. Modeling in air may therefore overestimate performance and underestimate tissue heating risks, which are central to safety claims. Because the paper uses simulation results to argue about parameter effects and “evading possible risks to living organisms,” the underlying material assumptions become a validity-critical methodological issue. The absence of tissue-equivalent modeling or validation in phantoms makes the translation of these results uncertain. Consequently, the claims about safe WPT behavior in vivo are insufficiently supported.\nFrom a health risk perspective, we are generally interested in how much EMF power is absorbed by biological tissues, as this is largely responsible for the heating effects described above. This is typically described as a function of a relevant dosimetric quantity. For example, below about 6 GHz, where EMFs penetrate deep into tissue (and thus require depth to be considered), it is useful to describe this in terms of “specific energy absorption rate” (SAR), which is the power absorbed per unit mass (W kg−1). ([2](#ref2))\nICNIRP’s guidelines explicitly identify heating as the substantiated health-relevant effect of RF exposure and emphasize dosimetric quantities like SAR for assessing absorbed power in tissue. This is directly relevant to a 15 MHz (i.e., well below 6 GHz) wireless power system intended to operate near or in the body, where tissue penetration and bulk heating can occur. The reviewed paper does not report SAR estimates, tissue temperature rise modeling, or compliance to RF exposure limits for the operating regime and geometry. Instead, it argues safety primarily from coil/heater IR observations and air-based simulation assumptions. Given ICNIRP’s emphasis on tissue heating and SAR as a measurement framework, the omission of dosimetry leaves the safety claim unsupported by standard practice. Therefore, the manuscript’s assertions about “minimum heat damage” in implant usage are not adequately justified.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|GPT|4", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "This paper’s claim that the robotic implant quantifies cardiac contractility is not convincingly supported because the reported measurements are strain-sensor readouts without sufficient calibration to established cardiac physiology metrics (and the manuscript sometimes interprets strain amplitude as myocardial strength/force).\n\nDemonstrations range from a robotic cuff encircling a blood vessel for detecting blood pressure, to a robotic gripper holding onto a bladder for tracking bladder volume, an ingestible robot residing inside stomach for pH sensing and on-site drug delivery, and a robotic patch wrapping onto a beating heart for quantifying cardiac contractility, temperature and applying cardiac pacing, highlighting the application versatilities and potentials of the nature-inspired soft robots.\nThis sentence explicitly claims “quantifying cardiac contractility” as a demonstration outcome, not just measuring strain or ECG. However, the later results primarily describe strain sensor signals on different cardiac chambers and interpret amplitude changes as “contractility patterns” and “myocardium strength.” Contractility in cardiovascular physiology is a loaded concept, often distinguished from deformation/strain and requiring careful control of loading conditions. Because the paper frames this as a key demonstration, the burden is on the manuscript to show how its sensor outputs map quantitatively to recognized indices of contractile function. Without a clear calibration/validation framework, the conclusion risks over-interpreting what the strain sensors actually measure. This weakens the reliability of the contractility-related conclusions.\nFigure 6 M& N show the contractility patterns of the right and left atria (RA and LA), and the right and left ventricles (RV and LV) under normal and MI conditions, respectively, measured by an implanted thera-gripper where the output features of the sensors are determined by their experienced strain that significantly correlates to their positions on epicardial surface. The S4 (LV) displays the largest amplitude due to a maximum experienced strain, indicating the intrinsic highest myocardium strength in the LV chamber. Figure 6 I reveals the area of infarction two weeks after the MI surgery. The results in Fig. 6 N demonstrate that the LV outflow obstruction changes patterns of ventricular contraction. The sensors S2 (RV) and S4 (LV) experience a reduced strain change due to the consequent loss of contractile myocardium, which, correspondingly, reduces force of myocardial contractility and decreases heart rate.\nThe quoted text equates measured strain patterns to “contractility patterns” and further interprets larger strain amplitude as higher “myocardium strength,” then infers reduced “force of myocardial contractility” from reduced strain change. Strain is a deformation measure that depends on both intrinsic myocardial properties and loading/boundary conditions; without calibration, strain amplitude alone is not a direct force/contractility measurement. The manuscript does not present a quantitative mapping from sensor strain signals to pressure-based or load-independent indices (e.g., pressure-volume analysis) that would justify the force/strength interpretation. While it references echocardiographic fractional shortening changes, it does not report a direct correlation between its strain-sensor outputs and validated contractile metrics under controlled conditions. This leaves room for alternative explanations (changes in contact mechanics, sensor placement, or loading) for amplitude differences. Consequently, the contractility conclusions are not as robust as the language implies.\nWith increasing consideration for rigor and reproducibility, the goal of this guidelines review is to provide best-practice information regarding how to measure accurately cardiac physiology in animal models. ([6](#ref6))\nThis guideline underscores that cardiac physiology measurement requires rigor and best practices, which is relevant when a new sensing modality claims to quantify contractility. The reviewed manuscript introduces a novel strain-sensing implant, but it does not provide the kind of validation detail (calibration, controls for anesthesia/heart rate/loading, and cross-method comparisons) that best-practice discussions emphasize. Because “contractility” is sensitive to measurement conditions, a high bar for validation is typical when proposing new implantable measurement approaches. The guideline thus supports the critique that stronger methodological grounding is necessary before asserting quantification of contractility, rather than deformation proxies. The paper’s current evidence is promising for strain sensing but does not meet the validation expectation implied by its contractility claims. This affects the robustness of the conclusions.\nDimensions and FS (these indexes can be reported but are fraught with error in this model), volumes, EF (if possible, 3D reconstruction), wall thickness ([6](#ref6))\nThis guideline text specifically cautions that dimension-based indexes like fractional shortening (FS) are “fraught with error” in myocardial infarction models, which are central to the reviewed paper’s MI demonstration. The reviewed manuscript uses FS decrease (75–15%) and echocardiographic strain imaging as contextual evidence of dysfunction, and then interprets its strain-sensor signals as contractility/force changes. If the contextual reference metrics are themselves error-prone in this model, that raises the need for careful cross-validation and robust measurement protocols when drawing contractility inferences. The paper does not show that its sensor-derived “contractility patterns” track a gold-standard or less load-dependent measure in MI (e.g., pressure-volume loops). Therefore, the guideline reinforces that the manuscript should be more conservative in interpreting MI-related contractility from strain readouts. This weakens confidence in the contractility-specific interpretation.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "The proposed actuation mechanism requires high power (~1 W) and elevated temperatures (40°C), which poses a severe risk of thermal damage to surrounding tissues, violating safety standards for implants.\n\n\"The PNIPAM hydrogel can undergo a notable volumetric change about 90% as the temperature change from 23°C to 40°C\"\nThis indicates that the device must be heated to 40°C to achieve full actuation. Given that the normal body temperature is 37°C, the margin for safety is extremely narrow (only 3°C). Local tissue heating to 40°C or slightly above can cause thermal damage or necrosis, especially if sustained for prolonged periods as required for drug delivery or monitoring.\n\"The saturation temperature of AgNW/PI nanocomposite heater increases with the supplied power as more Joule heat is generated, and the lower critical solution temperature (LCST) of PNIPAM hydrogel at 34°C can be obtained at low input power (< ~1W)\"\nThe statement implies that up to 1 W of power is required to reach the actuation temperature. Dissipating 1 W of power as heat within a small implantable device inside the body is highly unsafe. For context, safety standards for active implantable medical devices (e.g., ISO 14708-1) typically limit the temperature rise of the outer surface to 2°C above body temperature, which corresponds to much lower power dissipation (typically in the milliwatt range) [1].\n\"The wireless power transfer system achieves the highest harvested power ~ 1.05 W... which is sufficient to trigger the heater\"\nThis confirms that the system is designed to handle and dissipate around 1 W of power. Such high power dissipation in a confined space will inevitably lead to significant local heating of the surrounding tissue, posing a severe risk of thermal injury [2].\n\nReferences:\n[1] ISO 14708-1:2014 Implants for surgery — Active implantable medical devices — Part 1: General requirements for safety, marking and for information to be provided by the manufacturer. https://www.iso.org/standard/61603.html\n[2] Yarmolenko, P. S., Moon, E. J., Landon, C., Manzoor, A., Hochman, D. W., Viglianti, B. L., & Dewhirst, M. W. (2011). Thresholds for thermal damage to normal tissues: an update. International Journal of Hyperthermia, 27(4), 320-343. https://doi.org/10.3109/02656736.2010.534527", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "The reported wireless power transfer efficiency of 80% is unrealistically high for an implantable system and likely represents an idealized benchtop measurement rather than a practical in vivo scenario.\n\n\"the power efficiency reaches around 80%, which is sufficient to trigger the heater for raising local temperature to drive motions of the soft robot\"\nAchieving 80% power transfer efficiency for an implantable inductive link is exceptionally rare and contradicts established literature. Typical efficiencies for implantable wireless power transfer systems are significantly lower (often below 50%) due to factors such as low coupling coefficients, tissue absorption, and misalignment between coils [3]. The paper likely reports the coil-to-coil efficiency in air under ideal alignment, which is misleading for an implantable application where the receiver is embedded in lossy tissue and subject to movement.\n\"Fig. 4 K and Fig. 4 O exhibit a reduction in transmission efficiency resulting from decreased mutual inductance between the transmission and the receiving coils due to shape deformation.\"\nWhile the authors acknowledge a reduction in efficiency due to deformation, the baseline claim of 80% remains unsubstantiated for a realistic in vivo setup. Without specifying the conditions (e.g., distance, medium) under which this efficiency was measured, the claim exaggerates the system's performance and feasibility for deep-tissue implants [4].\n\nReferences:\n[3] Zargham, M., & Gulak, P. G. (2012). Maximum achievable efficiency in near-field coupled power-transfer systems. IEEE Transactions on Biomedical Circuits and Systems, 6(3), 228-245. https://doi.org/10.1109/TBCAS.2011.2174794\n[4] Ho, J. S., Kim, S., & Poon, A. S. (2013). Midfield wireless powering for implantable systems. Proceedings of the IEEE, 101(6), 1369-1378. https://doi.org/10.1109/JPROC.2013.2251851", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "The reliance on thermal actuation of bulk PNIPAM hydrogels inherently results in slow response times, which contradicts the paper's claims of \"real-time\" control and \"spatiotemporal precision\" for applications like cardiac pacing or bladder voiding.\n\n\"The PNIPAM hydrogel can undergo a notable volumetric change about 90% as the temperature change from 23°C to 40°C\"\nThe volume change of bulk PNIPAM hydrogels is governed by the diffusion of water molecules, which is a slow process. While the paper claims \"spatiotemporal precision,\" the response time for such bulk hydrogels is typically in the range of seconds to minutes, not milliseconds [5]. This slow response makes the device unsuitable for applications requiring rapid actuation, such as cardiac pacing or reacting to sudden changes in blood pressure.\n\"Fig. S18C, the flexible electrical heater exhibits steady heating and cooling cycles\"\nAlthough the figure is not provided here, the description of \"steady heating and cooling cycles\" implies a relatively slow thermal time constant. The cooling phase, in particular, relies on passive heat dissipation to the surrounding tissue, which is inherently slow and uncontrollable. This limits the frequency of actuation and the ability to perform rapid, repeated movements required for dynamic physiological environments [6].\n\nReferences:\n[5] Schild, H. G. (1992). Poly (N-isopropylacrylamide): experiment, theory and application. Progress in Polymer Science, 17(2), 163-249. https://doi.org/10.1016/0079-6700(92)90023-R\n[6] Zhang, X. Z., Xu, X. D., Cheng, S. X., & Zhuo, R. X. (2008). Strategies to improve the response rate of thermosensitive PNIPAAm hydrogels. Soft Matter, 4(3), 385-391. https://doi.org/10.1039/B713803M", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "While the paper claims biocompatibility, the use of Silver Nanowires (AgNWs) and PNIPAM raises long-term safety concerns due to potential leakage and cytotoxicity, which are not adequately addressed by the short-term experiments.\n\n\"mouse 3T3-J-2 cells exposed to complete soft robotic devices... remain robust healthy and maintain stable viability\"\nThe biocompatibility tests presented are short-term (likely days to weeks) and do not account for the long-term effects of implantation. Silver nanowires (AgNWs) are known to be cytotoxic and can cause oxidative stress if released into the body [7].\n\"curing process fully buries all the nanomaterials inside the PI matrix... This prevents separation of the nanomaterials from the polymeric matrix\"\nWhile the authors claim that the PI matrix prevents separation, the device is subjected to repeated mechanical deformation (bending, twisting, expanding). Over time, fatigue can cause micro-cracks in the PI matrix, leading to the leaching of AgNWs into the surrounding tissue. The paper does not provide long-term mechanical fatigue data combined with leaching tests to substantiate the safety of the encapsulation under chronic in vivo conditions [8].\n\nReferences:\n[7] AshaRani, P. V., Mun, G. L. K., Hande, M. P., & Valiyaveettil, S. (2009). Cytotoxicity and genotoxicity of silver nanoparticles in human cells. ACS Nano, 3(2), 279-290. https://doi.org/10.1021/nn800596w\n[8] De Jong, W. H., & Borm, P. J. (2008). Drug delivery and nanoparticles: applications and hazards. International Journal of Nanomedicine, 3(2), 133. https://doi.org/10.2147/IJN.S596", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Gemini|5", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "Despite the claim of \"softness\" and \"tissue-matching\", the use of Polyimide (PI) as the matrix for the e-skin introduces a significant mechanical mismatch with biological tissues, potentially causing stress concentrations and tissue damage over time.\n\n\"flexible nanocomposite layer... incorporated within a polymer matrix (e.g., polyimide)\"\nPolyimide (PI) has a Young's modulus in the GPa range (~2.5 GPa), which is orders of magnitude higher than that of soft biological tissues (kPa range) [9]. Even if the PI layer is thin and flexible, its high intrinsic stiffness creates a mechanical mismatch at the tissue-device interface.\n\"The as-fabricated soft robot can form a highly conformal interface with diverse biological surfaces, indicating its inherent mechanical softness\"\nThe claim of \"inherent mechanical softness\" is misleading because it conflates structural compliance (bending stiffness) with material softness (Young's modulus). While the device can bend to conform to surfaces, the high modulus of the PI matrix means that any local deformation or friction can generate high stresses on the tissue, leading to inflammation or fibrosis over long-term implantation [10].\n\nReferences:\n[9] Lacour, S. P., Courtine, G., & Guck, J. (2016). Materials and technologies for soft implantable neuroprostheses. Nature Reviews Materials, 1(10), 1-14. https://doi.org/10.1038/natrevmats.2016.63\n[10] Minev, I. R., Musienko, P., Hirsch, A., Barraud, Q., Wenger, N., Moraud, E. M., ... & Lacour, S. P. (2015). Electronic dura mater for long-term multimodal neural interfaces. Science, 347(6218), 159-163. https://doi.org/10.1126/science.1260318", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "The authors demonstrated the adhesion performance of the bio-adhesive layer using the bending image in Figure 3B, but this referee can’t find any quantified data set of the adhesion force, did the authors studied how strong it is under various conditions? (e.g. dry, wet environments, etc)", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "While the thickness of other layers was specified, the actuation hydrogel's thickness was missing (it seems to be considerably thick). Increase of the thickness might enhance actuation performance but could potentially affect sensing and stimulation properties.\n\n2-1) What is the optimal thickness of the actuation layer for achieving reliable shape-morphing?\n\n2-2) How does the thickness of the actuation layer affect sensing and stimulation performance?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "In Figure 3N, bending configurations appear to be different and uncontrollable although three arms had the same composition. Can the authors explain why? And, it seems those arms are not reversible since the off-arms don’t seem to return to the original state", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "In Figure 4A, there might be stability issues with the PAAM hydrogel as a pressure sensor. Considering the implant environment, swelling of the hydrogel might hinder pressure measurement due to instability in weight loss and capacitance changes. Any proposed solutions to address this concern would be necessary.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "The authors discussed the adhesion and actuation force of the hydrogel in Fig. S46, Supplementary Note S8. However, it seems to be considered in a dry environment. Given the nature of hydrogels, there might be swelling and degradation issues when operating in a wet environment.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "In Figures 5 and S47, the hydrogel was designed to face biological tissue (please correct me if not). In this case, some of physical sensors (e.g., strain and pressure gauges) would be fine, but how to figure out operation of other sensors/stimulators that need direct contacts to tissues? For example, the authors mentioned here electrical stimulation for the bladder, but is it possible to stimulate the bladder through the adhesive layer and PAAM hydrogel? That would be not. Can the authors explain how to achieve such functional operations?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "In Figure 5g, it is unclear what the author intended to demonstrate through the programming. Can the authors provide significance of the programming for the control of the bladder. (It is quite strange that E-stim ON when the bladder is void, and E-stim OFF after expansion/contraction cycle... Shouldn't it turn on when the volume reaches maximum?).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "In Figs. 6 and S52A, it appears difficult or impossible for the electronic components at the end of each arm to form a strong coupling to living tissues, particularly to tissues whose volume changes over time, such as the bladder. How did the authors control or attach the robotic arms?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_1|9", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "Page 3, line 86, It is not 'overactive', but 'underactive' bladder.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_1|10", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "In fig. 2c, is there a motivation for using such diverse materials for different components? This referee can’t find outstanding characteristics of those materials for sensing components.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_1|11", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "In figs. 2f and 2g, the authors claimed that soft robots can form conformal contacts to tissues, but did the authors study or compare mechanical modulus between devices and tissues?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_1|12", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "In fig. S12B, such layered structures are likely to interfere with each other's signals. is there any reason to measure both parameters at the same time? Or, even if simultaneous measurements are made, does each sensor operate independently?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_1|13", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "there's no description for Figs. 3H&3I", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_1|14", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "We usually do not include information about SI figures in main figure captions. For example, in fig.3, there is information about fig. S18 and 25, but these should be removed.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_1|15", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "please do double check all the figures including SI, whose order is a total mess", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "However, the devices used materials commonly used in practical applications, with the exception of an in situ solution-based fabrication approach, showing no significant material novelty. This article is also lack of either long-term feasibility or detailed information about the mechanism of each sensor like the relationships between pH, pressure and resistance.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "In the introduction part, some references (Nature Materials volume 15, pages937–950 (2016), Nature Nanotechnology volume 9, pages397–404 (2014), and Nature Electronics volume 6, pages779–789 (2023)) regarding stable tissue-interfacing performance of wearable/implantable devices should be cited to justify the authors’ research purpose.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "The reviewer believes that sensory-motor integration is valuable when the robot can control motors in response to signals received from sensors. However, it seems that controlling the motors and performing sensor functions operate independently. In that case, can this robot still be considered as the presence of responsiveness as mentioned in the introduction?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "It seems good that the robot is designed differently for each target organ. The reviewer is curious about the variation in curvature among different organs. For instance, in the case of organs like the heart and bladder, squeezing too much might make it challenging to grasp effectively. How was this consideration taken into account in the design?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "Why does the parallel strips configuration result in twisting? Is there any reference for this, or was it an original concept?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "On page 6, if the transfer method is well-designed, it could potentially enable multi-modal implementation. Is there a particular advantage in this solution-based approach over transfer methods?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "On Page 7, Figure 2H, the volume of the PNIPAM hydrogel in Figure 2H is shown to dramatically decrease between approximately 35°C and 45°C. Given that the normal human body temperature is around 36-37°C, even if actuation is induced by an electrothermal method, maintaining its shape seems crucial for attaching it to various organs within the body. To substantiate this point, it would be necessary for the authors to demonstrate volume changes starting from a range lower than 35°C.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "It was confirmed that the composite was implemented through XPS analysis. Is there a concern that this might result in lower performance compared to a full composite?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "After nanomaterials are created through the laser pattern, the inherent properties of the material make handling difficult. How was the surrounding material removed or treated?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|10", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "In Figs 3C, D, please indicate in the caption whether SEM images represent the surface or cross-section. Additionally, to determine the presence of voids, it may be necessary to examine cross-sectional TEM images.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|11", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "In Fig 3E, it is understood that accurately observing the exact temperature by performing twisting and bending may be challenging with an infrared camera. However, even considering this, it seems that the temperature distribution is not uniform.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|12", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "In Fig 3F, G, the temperature converges over time, but what is the reason for the continuous change in bending force? Additionally, once bent, how long does the bending force persist?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|13", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "In addition to comment 9, is it necessary to keep the heater on continuously to maintain actual bending when attaching it to an organ?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|14", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "The dual-axis graphs presented in this figure (Figure 3I, Figure 5F, K, N etc.) are difficult to intuitively comprehend. It is unclear whether the changes on the left axis correspond to the results on the right axis or if they were determined through variations in resistance, pressure, or pH values. Therefore, it seems necessary for the authors to modify the graphs for better intuitive understanding and provide explanations regarding the extent of numerical changes made.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|15", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "Using heat as a stimulus might potentially cause damage to the tissue. However, considering the hydrogel is thick enough, it may prevent such damage. How efficiently does heat transfer throughout the entire hydrogel, and is the heat dissipation effective enough to be considered safe?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|16", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "While applying temperature, can the thermal sensor accurately measure the temperature from the tissue?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|17", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "What is the reason for the difference in the transfer method in S12(b) compared to the dual printing method in S16?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|18", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "On Page 11, the author mentioned that “The electrothermal stimulus along with distributed sensing capabilities enables programmed actuation not only on demand but also regulated simultaneously by the sensing feedback”. How was actuation implemented based on sensing feedback?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|19", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "On Page 14, Figure S31, in Figure S31B, it is evident that there is a tendency for the coupling coefficient to decrease as the separation distance increases. However, in Figure S31D, there is a trend showing an increase in output power relative to input power as the distance increases. This observation appears to be theoretically inconsistent. If this graph is accurate, the authors need to provide additional explanations for these results.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|20", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "On Page 16, in order for the sensory robots developed by the authors to conformally adhere to tissues or organs, they require not only curvilinear surfaces but also effective adhesion. While this article mentions the adhesiveness of PNIPAM, a recently published paper indicates that PNIPAM shows tissue adhesion at low temperatures (around 25°C), but loses almost all adhesive strength when it transitions to a gel form near 40°C (Nature Biotechnology 2023, 41, 652–662). To showcase the tissue adhesion capability of the authors' device, it becomes imperative to gauge the adhesive strength of the hydrogel by varying temperatures. This would confirm that there are no issues with adhesion even after attaching it to an organ.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|21", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "In Figs 5, 6, the use of Au electrodes for electrical stimulation in electrotherapy seems somewhat divergent from the other sensing materials of this paper (Fig. S52B).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|22", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "In Fig 5G, the electrical stimulation off voltage is not 0.0 V. Is there a specific reason for this? To help readers to understand, it appears that the authors should provide additional explanations regarding the correlation between electrical stimulation and volume changes. Specifically, a clear clarification is needed on whether the specific electrical stimulation is causing an actual increase in volume or if it is transmitting signals to patients having urinary dysfunction.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|23", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "As the authors mentioned in the context, PNIPAM hydrogel has reversibly contract and relax property upon electrothermal trigger. If that's the case, is there no risk of delamination if the device is not well-adhered to the tissue when the internal body temperature decreases? Additionally, wouldn't there be a possibility that continuous electrothermal stimulation, applied to prevent deformation of the device after it is attached to the tissue, could have adverse effects on the tissue?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|24", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "On Page 24, Figure 6F, what is the indication T1 and T2 in Figure 6F account for? The authors need to explain these in the caption.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|25", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "In Fig 6G, it is challenging to consider it as functioning like a pacemaker, as pacing does not seem to lead to actual cardiac capture.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|26", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "In Figs 6 M, N, it was mentioned that changes were observed in S2 and S4. However, it seems that only changes in frequency are visible along the x-axis. Shouldn't the focus be on the resistance changes along the y-axis, which may represent actual strain changes?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|27", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "The paper lacks details on the system used to generate water flow simulating blood flow in the vascular system, including names of the equipment and the setting of flow rate. Information on the properties and thickness of the rubber used is also insufficient.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|28", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "This work validated through H&E staining data that a single-day stimulation has a minimal impact on the tissue. However, it remains unclear what effects may occur with continued stimulation over longer period.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|29", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "The 2-week histological analysis of cardiac tissue with a hydrogel-based thera-gripper, as presented in the study, raises questions. It would be insightful to know the condition of the device after this period –whether the device remained in an operable state and the device remained properly attached as intended while withstanding repeated pulsations.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|30", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "Caption in figure S11 (a) : AgNW/PI -> AgNW/PDMS", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|31", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "Page 21, the third line from the bottom spelling error : PINPAM -> PNIPAM", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|32", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "Figure S51D, indication spelling error : Basi -> Basic", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|84|Human_2|33", "source": "prb", "split": "test", "paper_id": "prb84", "comment": "There should be a space before the units in the text and figures.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Claude|1", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "The paper repeatedly asserts a \"link\" between chromosome folding, gene expression, and genome evolution, but all evidence presented is correlational without any perturbation experiments or mechanistic validation to establish causality.\n\n\"Altogether, our results reveal that S. ambofaciens' linear chromosome is partitioned into structurally distinct entities, indicating a link between chromosome folding, gene expression and genome evolution.\"\nThe abstract makes a strong claim about a \"link\" between three complex phenomena. However, the paper only demonstrates temporal correlations between changes in transcription and changes in chromosome architecture. No experiments are performed to test whether manipulating one variable (e.g., transcription) causally affects the others (e.g., chromosome folding). Standard approaches in the field such as transcription inhibition experiments, NAP/SMC mutants, or inducible gene expression systems would be needed to establish causality rather than correlation.\n\"Collectively, these results indicate a link between evolutionary processes, including genome-compartmentalization and the molecular mechanisms (e.g. transcription, 3D-folding) that shape the structure and function of genes and genomes in Streptomyces.\"\nThis concluding statement again uses \"link\" language without distinguishing between correlation and causation. The evolutionary connection is particularly speculative since no phylogenetic comparisons of chromosome organization across Streptomyces species are performed, nor are any experimental evolution studies presented. The claim that transcription and 3D-folding \"shape\" genome structure implies directionality that is not tested experimentally.\n\"At larger scales, there is an increase in the frequency of inter-arm DNA contacts. The most likely candidate to be involved in this reorganization is the Smc-ScpAB condensin complex, which is recruited to the origin region by ParB bound to parS.\"\nThe paper hypothesizes that Smc-ScpAB is responsible for chromosome compaction but does not test this experimentally. The authors cite an \"accompanying paper\" (Szafran et al.) that apparently demonstrates this in S. venezuelae, but for the current study in S. ambofaciens, no such mechanistic validation is performed. Without SMC knockouts or depletion experiments, the role of condensin in the observed conformational changes remains speculative.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Claude|2", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "The paper acknowledges that different biological replicates show different patterns of SMBGC expression and boundary formation during metabolic differentiation, but does not provide systematic quantification of this variability or statistical analysis of replicate consistency, despite this variability having implications for the reproducibility of key conclusions.\n\n\"In a replicate experiment, we observed that the expression of another SMBGC, encoding the biosynthesis of a siderophore, could generate the formation of an additional boundary (Supplementary Fig.3.C). This illustrates some variability in the expression of SMBGCs during metabolic differentiation.\"\nThis statement reveals that different biological replicates show fundamentally different patterns of SMBGC expression and boundary formation at 48h. The congocidine BGC forms a boundary in the main experiment (Figure 4E), while a siderophore BGC forms an additional boundary in a replicate (Supplementary Fig.3.C). Although two independent 3C-seq experiments were performed per condition, no statistical analysis is presented comparing boundary positions across replicates or correlating boundary detection with SMBGC expression levels across replicates. This raises questions about which observations are reproducible features versus stochastic variations.\n\"Together, these results highlight the correlation between SMBGC expression and the formation of boundaries after 48 h.\"\nThis conclusion about correlation between SMBGC expression and boundary formation is drawn despite the acknowledged replicate variability. For a robust correlation analysis, one would expect quantification across multiple replicates showing that when a specific SMBGC is expressed at high levels, a boundary reproducibly forms at that location. Instead, the main figures show single representative experiments with replicates relegated to supplementary figures, and no formal correlation analysis across replicates is presented.\n\"For the 3C-seq analyses, two independent experiments (performed on different days) were carried out for each condition.\"\nWhile two biological replicates were performed, the paper does not present a systematic comparison of boundary positions between replicates. Given that the frontier index method identifies boundaries based on threshold-crossing (median plus 2 standard deviations), it would be informative to know what fraction of boundaries are reproducibly detected in both replicates versus detected in only one. The observation that different SMBGCs form boundaries in different replicates suggests this reproducibility analysis is important but absent.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Claude|3", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "The comparison between 24h (exponential phase) and 48h (metabolic differentiation) timepoints involves numerous physiological changes beyond metabolic differentiation, including nutrient depletion, growth rate reduction, and changes in cell density, yet the paper attributes observed changes primarily to metabolic differentiation without controlling for these confounding factors.\n\n\"To focus specifically on transcriptome dynamics during metabolic differentiation, while limiting cellular physiological heterogeneity in the colony, we took advantage of the fact that S. ambofaciens, like many Streptomyces, does not sporulate in liquid medium.\"\nThe authors acknowledge the need to limit physiological heterogeneity but only address sporulation. Liquid culture at 48h versus 24h involves many other physiological differences: nutrient depletion (glycerol and nitrogen sources), accumulation of metabolic byproducts, changes in growth rate, different cell densities, and potentially different cell ages. None of these factors are experimentally controlled or even measured. For example, the MP5 medium conditions at 48h could simply reflect a generic stress response to nutrient limitation rather than a specific \"metabolic differentiation\" program.\n\"The results showed that the transcriptomes were rather similar in exponential phase in both media, while commitment to specialized metabolism (C4, C5 and C7 conditions) was accompanied by major transcriptional changes that form a distinct cluster\"\nThe clustering of late timepoints (C4, C5, C7) together is interpreted as evidence for \"commitment to specialized metabolism.\" However, these conditions also share features like reduced growth rate and nutrient depletion that could explain transcriptional similarity independent of specialized metabolism. The YEME 48h condition (C7) shows some antibiotic production but much less than MP5 48h (C4), yet they cluster together, suggesting that factors beyond antibiotic production drive the transcriptional changes.\n\"Whereas the cluster 1 corresponds to exponential phases (no ATB production), the cluster 2 gathers conditions associated to the activation of SMBGC encoding at least two known antibacterial activities\"\nThis interpretation conflates correlation with causation. Cluster 2 includes conditions with antibiotic production, but it also includes conditions with slow growth, high cell density, and nutrient depletion. To establish that SMBGC activation specifically drives the chromosome remodeling, one would need to decouple these factors—for example, by comparing cells at the same growth phase but with genetically activated or repressed SMBGCs.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Claude|4", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "The paper's major conclusions about chromosome compartmentalization and remodeling rely exclusively on 3C-seq data without validation through independent methods such as fluorescence in situ hybridization (FISH), chromosome painting, or super-resolution microscopy, which limits the ability to independently verify the claimed structural changes.\n\n\"Altogether, our results reveal that S. ambofaciens' linear chromosome is partitioned into structurally distinct entities\"\nThe claim that the chromosome is \"partitioned into structurally distinct entities\" is based solely on 3C-seq contact frequency analysis. While 3C-seq provides valuable population-averaged information about DNA contacts, it does not directly visualize chromosome structure. Studies of bacterial chromosome organization have commonly validated 3C/Hi-C findings with FISH or other imaging approaches to confirm that contact frequency patterns reflect actual spatial organization. Without such validation, the \"structural\" claims remain inferences from biochemical data rather than direct observations.\n\"In exponential phase, the chromosome of Streptomyces is organized into one transcriptionally active (light green) central compartment and two rather silent compartments (pink grey). [...] After 48 h of growth, the transcription of the congocidine cluster is accompanied by a global remodeling of the chromosome.\"\nThe schematic model (Figure 4F) depicts dramatic changes in chromosome conformation from \"open\" to \"closed,\" but these representations are interpretations of contact frequency data, not direct observations of physical structure. The transition from an open conformation (low inter-arm contacts) to a closed conformation (high inter-arm contacts) could reflect changes in chromatin compaction, changes in protein-DNA interactions, or changes in cellular physiology affecting crosslinking efficiency. FISH experiments targeting specific loci on each arm could directly test whether the physical distance between arms decreases during metabolic differentiation.\n\"The contact probability, P(s), plotted as a function of genomic distance in exponential phase in YEME medium (C6 condition). The plot represent the intra-chromosomal contact probability, P(s), for pairs of loci separated by a genomic distance (in base pairs) on the chromosome\"\nThe P(s) analysis is a standard approach for Hi-C/3C-seq data interpretation, but it provides population-averaged measurements that may not reflect the behavior of individual cells. Single-cell imaging approaches would help determine whether all cells in the population undergo the same conformational transition or whether the observed changes reflect shifts in cell population composition. This is particularly relevant given the acknowledged variability in SMBGC expression between replicates.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|GPT|1", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "This paper’s transcriptome analyses comparing growth conditions (e.g., Fig. 2 / Extended Data Fig. 1–2 and downstream claims about metabolic differentiation-associated transcriptional changes) are not reliably supported because one key condition (C5, 72 h) was prepared with a different RNA-seq library kit than all other conditions, yet the statistical modeling description does not indicate any batch-factor control for this protocol change.\n\nDirectional RNA-seq libraries were constructed using the Illumina ScriptSeq kit V2 (discontinued) for samples corresponding to C5 conditions and Illumina Stranded library preparation kit for all other samples, according to the manufacturer’s recommendations.\nUsing different library preparation chemistries for different conditions is a classic source of batch effects because it changes fragmentation/priming/strand bias and other technical properties that affect observed counts. Here, the protocol switch aligns exactly with a biological factor of interest (C5 is a late time point during antibiotic production), so technical and biological effects are partially confounded. Because the paper’s central narrative relies on comparing expression dynamics across time points and media, any systematic shift in counts attributable to library chemistry can distort clustering, differential expression, and “switch”/category assignments. The manuscript does not describe including “library kit” (or any proxy) as a covariate, nor does it present sensitivity analyses that repeat key conclusions excluding C5. This is significant because a single outlier condition can drive correspondence analysis, PCA structure, and the perceived magnitude of “metabolic differentiation” transcriptomic remodeling. A robust design would either keep library chemistry constant or explicitly model and validate the batch contribution.\nThe reference condition was C1 (medium “MP5_24h”). All parameters of SARTools that have default values were kept unchanged.\nThis statement implies the analysis was run with default settings, but it does not specify a design formula that accounts for protocol-induced batch structure across the 37 samples. In DESeq2-style GLMs, failing to include a relevant batch factor can lead to biased effect-size estimates and false positives/negatives when batch correlates with condition. Because the paper uses global multivariate analyses (PCA/clustering/correspondence analysis) and differential expression to support high-level biological interpretations, unaccounted technical structure is a major threat to validity. The lack of an explicit model term (e.g., library preparation kit) also makes the analysis hard to audit or reproduce. The manuscript would be substantially stronger if it reported model formulas, demonstrated that C5 is not a batch-driven outlier, and showed that conclusions hold when controlling for library chemistry.\n```r\nvarInt <- \"group\"                                    # factor of interest\ncondRef <- \"WT\"                                      # reference biological condition\nbatch <- NULL                                        # blocking factor: NULL (default) or \"batch\" for example\n```\nThe provided code base includes a template explicitly supporting a blocking/batch factor, indicating that the underlying workflow can incorporate batch effects when needed. However, the manuscript’s methods do not indicate that such a factor was used to address the library preparation change specific to C5. This mismatch matters because it highlights a straightforward, commonly used remedy that is not documented as applied. Even if the authors believe the kit difference is negligible, best practice is to either model it or provide empirical evidence (e.g., QC plots stratified by kit) showing it does not drive results. Without that, readers cannot distinguish biological time-course structure from protocol artifacts. Given the importance of transcriptome dynamics to the paper’s conclusions, this omission is a major methodological gap.\nOne often overlooked complication with such studies is batch effects, which occur because measurements are affected by laboratory conditions, reagent lots and personnel differences. This becomes a major problem when batch effects are correlated with an outcome of interest and lead to incorrect conclusions. [1](https://pubmed.ncbi.nlm.nih.gov/20838408/)\nThis directly articulates the general statistical risk created by the paper’s design choice: a technical factor (library kit) is aligned with the biological variable (late differentiation time point), which can induce spurious condition effects. The quote is especially relevant because it emphasizes correlation between batch and outcome as the failure mode, which matches this study’s setup. It also underscores that batch effects are not esoteric edge cases but common, high-impact artifacts in high-throughput assays. In this manuscript, the C5-specific protocol change is a concrete, documented source of such artifacts. Without an explicit correction or validation, the paper’s differential expression and clustering-based inferences are vulnerable to exactly the “incorrect conclusions” mechanism described. This is a substantial validity issue rather than a minor reporting preference.\nThe use of linear models, however, provides the flexibility to also analyze more complex designs, as is often useful in genomic studies [ 15 ]. [2](https://genomebiology.biomedcentral.com/articles/10.1186/s13059-014-0550-8)\nThis sentence summarizes a key reason batch effects are routinely addressed in RNA-seq: GLM-based frameworks can incorporate additional covariates (such as batch or protocol) without abandoning differential expression testing. Because the paper already uses a DESeq2-based pipeline, the methodological barrier to handling the C5 kit change is low; it is largely a matter of specifying and reporting the design. The quote strengthens the criticism by showing that the field-standard statistical approach the authors chose is explicitly intended for complex experimental designs, including non-biological structure. Consequently, omitting a documented, condition-linked protocol change from the model is not aligned with common practice. This omission undermines confidence in the paper’s interpretation of transcriptome dynamics, particularly those relying on cross-condition comparability. The manuscript would need to demonstrate that the main patterns persist under a model that accounts for the library-kit batch.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|GPT|2", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "This paper’s conclusion that metabolic differentiation drives a global “open-to-closed” remodeling of Streptomyces chromosome conformation (e.g., Fig. 4E–F) is not robust because the 3C-seq contact maps are obtained from asynchronous populations and are interpreted in terms of cell-cycle state, yet the experimental design does not control for replication/cell-cycle composition across conditions.\n\nThe normalized contact map was obtained from asynchronous populations.\nAsynchronous cultures contain a mixture of replication states and cell-cycle stages, and 3C/Hi-C maps from such populations are averages over these subpopulations. Because chromosome folding features (e.g., inter-arm alignment, secondary diagonals, origin-domain behavior) can be cell-cycle dependent, changes in the population’s stage distribution between 24 h and 48 h can produce apparent “remodeling” even without a differentiation-specific mechanism. The manuscript does not report synchronization, replication profiling, or explicit modeling of mixture effects, so the attribution of differences specifically to metabolic differentiation is underdetermined. This is especially important because the paper later invokes “late in the cell cycle” as an interpretation, acknowledging the relevance of cell-cycle state. Without controlling or measuring it, the same data are consistent with alternative explanations (growth-phase/cell-cycle redistribution) that weaken the causal conclusion. This is a major interpretational vulnerability, not a minor limitation, because the open/closed remodeling is a central, highly emphasized result.\nThis suggests that late in the cell cycle and in the absence of a central compartment segmented into multiple domains, the two chromosome arms are closer to each other (Fig.4.E & F).\nThe paper explicitly links the observed secondary diagonal/inter-arm contact increase to “late in the cell cycle,” but it does not demonstrate that the sampled populations are matched in cell-cycle composition across conditions. This statement makes the confound particularly acute: the authors’ own biological interpretation relies on a variable (cell-cycle stage) that was not experimentally controlled. If the 48 h culture contains a higher fraction of cells at later replication/segregation stages than the 24 h culture, the observed contact-map differences could follow directly. Moreover, the paper’s broader framing attributes remodeling to metabolic differentiation, but this sentence indicates a plausible alternative mechanism. A robust causal claim would require direct cell-cycle measurements (e.g., DNA content, replication marker profiling) or synchronized sampling. In the absence of such controls, the conclusions about differentiation-driven architectural switching are not securely supported.\nThese domains are stable throughout the cell cycle and are reestablished concomitantly with DNA replication. [3](https://pmc.ncbi.nlm.nih.gov/articles/PMC3927313/)\nThis external result highlights that bacterial chromosomal domain structure and its re-establishment are intimately linked to replication/cell-cycle processes, reinforcing the plausibility of cell-cycle-driven changes in population Hi-C/3C maps. It shows that cell-cycle dynamics are not a peripheral effect but a central determinant of domain architecture in bacteria. In the context of the reviewed paper, it means that differences between exponential and later-growth samples can reflect replication-associated restructuring rather than (or in addition to) differentiation-specific transcriptional programs. Because the paper’s key claim is a global conformational switch across growth/differentiation time points, replication-linked architecture provides a direct alternative explanation. The quote therefore supports the criticism that controlling for cell-cycle composition is essential for causal attribution. Without such control, the manuscript’s conclusion overstates what the data uniquely imply.\nHere, we combine super-resolution microscopies and chromosome-capture technologies to unravel the higher-order organization of the Bacillus subtilis chromosome and its dynamic rearrangements during the cell cycle. This organization, along with global folding throughout the genome, is present before replication, disrupted by active DNA replication, and re-established thereafter. [4](https://pubmed.ncbi.nlm.nih.gov/26295962/)\nThis provides direct evidence (in a different bacterial system) that chromosome-capture signals can undergo large-scale reorganization across the cell cycle and in response to replication activity. The statement that global folding is disrupted and re-established around replication emphasizes how strongly replication-state mixtures can shape ensemble contact maps. In the reviewed paper, the primary comparison is between 24 h and 48 h cultures that likely differ in growth physiology, replication dynamics, and nucleoid state. The cited work supports the idea that without measuring replication status, large architectural differences cannot be uniquely assigned to “metabolic differentiation.” It also shows that “global remodeling” is not unprecedented as a cell-cycle/replication phenomenon, weakening novelty claims tied to differentiation. This strengthens the criticism that the paper’s interpretation is not adequately controlled for known confounders.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|GPT|3", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "This paper’s mechanistic interpretation that transcription dynamics (including SMBGC activation) drive boundary formation and that Smc-ScpAB loop extrusion underlies global inter-arm contact increases is not adequately supported because the presented data are correlational and no direct perturbations (e.g., transcription inhibition, locus relocation, Smc/ParB disruption) are performed in Streptomyces to test these causal links.\n\nTo determine whether transcription dynamics influence the 3D-organization of the chromosome, we performed 3C-seq on Streptomyces cells during metabolic differentiation in MP5 medium (48 h, condition C4) (Fig.4.E). ... the appearance of a very sharp boundary within the right terminal region ... correlates very well with the increased level of transcription of the congocidine biosynthetic gene cluster (BGC, Fig.4.B & E).\nThe manuscript frames the experiment as testing whether transcription “influences” 3D organization, but the design is observational: transcription and contacts are measured under different time points/conditions without an intervention separating cause from consequence. The inference rests on a correlation (“correlates very well”), which cannot exclude alternative drivers such as replication-state shifts, changes in nucleoid proteins, or mapping/normalization artifacts that co-vary with growth phase. Importantly, no experiment disrupts congocidine expression independently of growth state to test whether the boundary disappears, nor does the paper ectopically induce the cluster to test whether a boundary appears. Because the boundary/SMBGC linkage is central to the proposed “relocation of transcriptional hubs,” the lack of causal tests is a major weakness. Correlation can motivate hypotheses, but the manuscript’s wording and schematic (Fig. 4F) imply a stronger causal mechanism than is demonstrated. The conclusions should therefore be tempered or supported with perturbation experiments.\nAt larger scales, there is an increase in the frequency of inter-arm DNA contacts. The most likely candidate to be involved in this reorganization is the Smc-ScpAB condensin complex ... Smc-ScpAB promotes inter-arm contacts by translocating to the terminal region of the chromosome, likely by loop extrusion.\nThis is a specific mechanistic proposal (Smc-ScpAB-driven loop extrusion) for the global architectural change, but the paper does not present Streptomyces-specific functional evidence (e.g., Δsmc/ΔparB mutants, Smc depletion, ParB/parS perturbation, or Smc ChIP-seq) to support it. Because multiple factors can affect inter-arm contacts (replication progression, transcriptional interference with condensins, changes in nucleoid-associated proteins), calling Smc “the most likely candidate” without direct tests risks overinterpretation. The manuscript also uses this mechanism to interpret subtle features (tilt of the secondary diagonal), which further compounds uncertainty when the causal actor is unverified. In contrast to descriptive statements (“we observed”), mechanistic attribution requires either perturbation or orthogonal measurement of the proposed factor’s activity. The cited bacterial literature motivates plausibility, but plausibility is not evidence for the specific system/conditions studied here. This weakens the reliability of the mechanistic conclusions even if the descriptive contact-map changes are real.\nTo probe the role of gene expression in chromosome structure, we performed Hi-C on swarmer cells treated for 30 minutes with rifampicin (rif), an inhibitor of transcription elongation ( 12 ). ... However, CID boundaries were severely disrupted in rif-treated cells leading to a nearly domain-free organization ( Fig. 2B , S18–19 ). [3](https://pmc.ncbi.nlm.nih.gov/articles/PMC3927313/)\nThis provides a clear example of the type of causal experiment that can substantiate a transcription-to-boundary mechanism: transcription is directly perturbed while measuring chromosome conformation. The result that boundaries are “severely disrupted” after inhibiting elongation shows that boundaries can be causally dependent on transcriptional processes, not merely correlated. In the reviewed paper, no analogous transcription perturbation is performed in Streptomyces during the relevant growth stages, so the causal direction remains ambiguous. The external evidence therefore sharpens the criticism: the field has established feasible, informative perturbations, and the manuscript does not use them despite making similarly mechanistic claims. Without such tests, the manuscript’s mechanistic framing goes beyond what its data support. This is a significant issue for conclusions because it affects whether the paper demonstrates a mechanism or only reports associations.\nWe also moved the highly-expressed gene rsaA to the vanA locus, a poorly expressed region of the genome ( fig. S22 ). ... insertion of rsaA generated a sharp new CID boundary at this position in the genome ( Fig. 2C ). ... We conclude that highly-expressed genes play a direct role in defining chromosomal domain boundaries. [3](https://pmc.ncbi.nlm.nih.gov/articles/PMC3927313/)\nThis locus-relocation experiment demonstrates causality even more directly: introducing a highly expressed gene into a new genomic context creates a new boundary at that position. It therefore provides a strong benchmark for what is needed to claim that specific transcriptional units (e.g., SMBGCs) “form new boundaries.” The reviewed paper’s SMBGC-boundary linkage is based on co-occurrence in time/condition, not on manipulating expression independently of genomic position and global physiology. Because Streptomyces SMBGCs are large and embedded in specialized regulatory contexts, relocation or inducible activation experiments would be especially informative for disentangling transcriptional effects from cluster-specific chromatin factors. The absence of such causal tests means the manuscript cannot distinguish whether transcription creates the boundary or whether boundary formation reflects other processes that enable transcription. The external quote thus directly contradicts the sufficiency of purely correlational evidence for a causal conclusion.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|GPT|4", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "This paper’s conclusions about boundary gain/loss across growth phases (especially the disappearance of central boundaries and appearance of SMBGC-associated boundaries) are not sufficiently supported because the boundary-calling procedure is highly threshold/heuristic-driven on noisy 3C-seq data, replicate variability is acknowledged, and no quantitative reproducibility/quality assessment is reported.\n\nNote that due to intrinsically noisy nature of 3C-seq data, we detected bins with only an upstream or a downstream significant peak (Supplementary Fig.3.D). These bins with an ‘orphan’ peak were not associated with a boundary, and hence, were removed from the analysis.\nThis passage is an explicit acknowledgment that the core signal used to define boundaries (frontier-index peaks) is noisy enough to frequently produce one-sided peaks. Discarding “orphan” peaks is a defensible heuristic, but it means boundary calls depend strongly on the joint significance threshold and on noise properties that can vary across conditions (e.g., depth, ligation efficiency, restriction-site distribution, mapping). Because the paper’s biological conclusions hinge on the presence/absence of boundaries, sensitivity of boundary detection to noise and thresholding is a major uncertainty source. The manuscript does not quantify how often boundaries are near-threshold, how stable boundary positions are across replicates, or how results change under reasonable parameter variations (e.g., peak cutoff, distance window). Without these robustness checks, claims like “boundaries … were not detected anymore” could reflect detection failure rather than biological disappearance. The paper’s own methods section therefore supplies direct evidence that boundary calls may be brittle. This undermines confidence in boundary dynamics as a firm basis for biological interpretation.\nIn a replicate experiment, we observed that the expression of another SMBGC, encoding the biosynthesis of a siderophore, could generate the formation of an additional boundary (Supplementary Fig.3.C). This illustrates some variability in the expression of SMBGCs during metabolic differentiation.\nThis shows that the boundary landscape during metabolic differentiation is not consistent even across replicates under nominally the same condition, with different SMBGCs forming boundaries in different experiments. If boundary formation is variable, then the paper’s general conclusion that SMBGC expression “forms new boundaries” needs a stronger statistical characterization (e.g., frequency across replicates, effect sizes, confidence intervals for boundary strength). The manuscript treats this as illustrative variability rather than as a quantitative uncertainty that propagates to its main claims. Moreover, variability in SMBGC expression suggests that population heterogeneity and stochastic activation may be substantial, which complicates interpretation of ensemble 3C-seq maps. Without reproducibility metrics, it is unclear whether reported boundary changes are robust features or contingent outcomes. This is significant because the paper’s mechanistic narrative depends on reliably identifying boundaries and tracking their changes.\nThe detection of bins with only an upstream or a downstream significant peak reflects the intrinsically noisy nature of 3C-seq data.\nThis supplementary legend reinforces that noise is not a minor nuisance but an intrinsic property of the measurement in this study’s setting. When the primary analytical objects (boundaries) are defined via peak detection, intrinsic noise implies a nontrivial false-negative/false-positive boundary rate unless carefully calibrated. The manuscript does not report boundary-calling precision/recall proxies, replicate concordance, or any metric of boundary reproducibility, despite this known noise. As a result, readers cannot evaluate how much uncertainty to assign to the boundary counts, locations, or their condition-specific changes. In addition, the paper does not discuss whether sequencing depth or coverage differences between conditions could change the noise distribution and thereby the number of “significant” peaks. This directly affects the reliability of the conclusions about remodeling.\nHi-C experiments are costly to perform and involve multiple complex experimental steps; thus, accurate methods for measuring the quality and reproducibility of Hi-C data are essential to determine whether the output should be used further in a study. [5](https://pubmed.ncbi.nlm.nih.gov/30890172/)\nThis quote establishes a widely recognized standard in the chromosome-conformation field: because the assay is complex and noisy, explicit reproducibility/quality assessment is essential, not optional. The reviewed paper’s boundary-centric claims depend on subtle features in contact maps and on peak-detection procedures, which are exactly the kind of outputs sensitive to experimental variability. Yet, beyond showing a single replicate figure, the manuscript does not provide quantitative reproducibility metrics (e.g., replicate concordance measures, replicate QC scores, boundary overlap statistics). The cited work also notes that naive comparisons can be deficient, implying that a rigorous assessment should use methods tailored to contact-map data. In the absence of such evaluation, the manuscript’s claims about boundary dynamics remain insufficiently supported. This is a significant methodological weakness because it affects whether the reported remodeling is reproducible and therefore publishable as a robust biological finding.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|GPT|5", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "This paper does not provide enough executable, study-specific computational material to reproduce key results (comparative genomics compartment calls, RNA-seq summaries, and especially 3C-seq processing and frontier-index boundary calling), because it relies on a custom web tool and describes complex processing steps without releasing the exact code/configuration used; the included code folder is a generic SARTools distribution rather than the analysis pipeline used for this study.\n\nWe designed the Synteruptor program (http://bim.i2bc.paris-saclay.fr/synteruptor/)⁶⁰ to compare the sequences of chromosomes of species close enough to have synteny blocks, and to identify the genomic islands existing in each respective chromosome.\nA custom tool can be appropriate, but reproducibility requires that readers can obtain the exact implementation and version used, along with parameters and input genome sets. Here, the method depends on thresholds (e.g., the “15 CDS” rule) and on how synteny blocks are computed and filtered, which can materially affect GI calls and thus downstream claims about compartmental enrichment. A web-hosted tool URL alone does not ensure long-term accessibility, versioning, or auditability of the algorithmic details. The manuscript does not provide a snapshot of the tool’s code, a container, or a commit hash corresponding to the analyses reported. This makes it difficult to reproduce GI annotations or to verify robustness to parameter choices. Because comparative-genomics compartment definitions are used as a backbone for later interpretations, this is a significant reproducibility gap.\nThe datasets generated during this study have been deposited in the NCBI Gene Expression Omnibus (GEO, https://www.ncbi.nlm.nih.gov/geo/) under the accession number GSE162865.\nDepositing raw data is necessary and valuable, but it is not sufficient for computational reproducibility of derived figures and boundary calls. The paper’s analysis includes multiple nontrivial steps (adapter-based duplicate removal, Bowtie2 filtering, binning, SCN normalization, P(s) subtraction, pseudocounting, derivative-based FI computation, peak calling, and orphan-peak filtering) where parameter choices can change results. Without releasing the scripts/configs that implement these steps exactly, reanalysis from GEO is time-consuming and error-prone, and small implementation differences can yield different boundary sets. This matters because the central claims depend on detecting condition-specific boundaries and secondary diagonals. Providing data without the full workflow also limits the community’s ability to extend the analysis to other Streptomyces datasets in a consistent way. Thus, while the GEO deposition supports transparency, it does not resolve the paper’s reproducibility shortcomings.\nSARTools is a R package dedicated to the differential analysis of RNA-seq data. It provides tools to generate descriptive and diagnostic graphs, to run the differential analysis with one of the well known DESeq2 or edgeR packages and to export the results into easily readable tab-delimited files.\nThe “code” included with the preprint is primarily a general-purpose RNA-seq analysis package description rather than a project-specific analysis repository that re-creates the manuscript’s figures and tables. This is important because the paper’s distinctive contributions are the integration of RNA-seq with 3C-seq and the frontier-index boundary analysis, neither of which is captured by distributing a generic differential-expression pipeline alone. Even for RNA-seq, a package README does not specify which target/design files, contrasts, filtering steps, and normalization outputs were used to generate the reported categories and contingency-table analyses. For 3C-seq and comparative genomics, the absence of scripts is even more consequential, as those analyses include custom boundary calls and compartment statistics. As a result, readers cannot reproduce the end-to-end computational path from raw data to the key claims. This is a major methodological limitation for a multi-omic computational study.\n```r\nworkDir <- \"C:/path/to/your/working/directory/\"      # working directory for the R session\nprojectName <- \"projectName\"                         # name of the project\nauthor <- \"Your name\"                                # author of the statistical analysis/report\n```\nThis template script indicates that the provided code is an example scaffold rather than the specific script used for the study (it contains placeholder paths and generic variable names). While templates are useful for general users, they do not substitute for the precise, versioned scripts and parameter files that reproduce a paper’s reported outputs. In particular, a reproducible paper package would include the actual design/target files, the exact contrast definitions, and a way to regenerate Supplementary Table 5 and figure panels from the deposited data. The presence of placeholders also signals that the repository is not tied to the manuscript’s data structure, making it unlikely that a reader could run it without substantial reconstruction work. This directly affects reproducibility and auditability of the transcriptome results, even before considering 3C-seq processing. Therefore, the code as provided does not meet the expectations for reproducible computational research in a multi-omics study.\nFor every involved step, you should ensure that every detail that may influence the execution of the step is recorded. If the step is performed by a computer program, the critical details include the name and version of the program, as well as the exact parameters and inputs that were used. [7](https://journals.plos.org/ploscompbiol/article?id=10.1371/journal.pcbi.1003285)\nThis directly states the reproducibility standard that the reviewed paper does not meet for its most complex analytical components (3C-seq processing and FI boundary calling). While the manuscript lists some tools (e.g., Bowtie2, STAR, Cutadapt) and broad procedures, it does not provide the exact command lines, configuration files, or code implementing key processing and filtering steps that can influence outputs. In addition, custom steps (e.g., outlier replacement in matrices, peak thresholding, compartment-specific statistics) are described narratively but are not packaged as runnable workflows. The quote also emphasizes recording inputs, which in this case includes genome versions, restriction fragment maps, and binning/normalization parameters. Without these details in executable form, independent researchers cannot reliably reproduce boundary sets and downstream enrichment analyses. This is a significant weakness for a paper whose primary contributions are computational interpretations of high-throughput data.\nThere is an urgent need to improve the infrastructure supporting the reuse of scholarly data. ... the FAIR Principles put specific emphasis on enhancing the ability of machines to automatically find and use the data, in addition to supporting its reuse by individuals. [6](https://pubmed.ncbi.nlm.nih.gov/26978244/)\nThe FAIR principles highlight that reuse requires more than raw deposition: it requires well-described, machine-actionable metadata and workflows that enable others to find, interpret, and recompute results. In the reviewed manuscript, although GEO access is provided, the absence of a complete, scripted analysis pipeline for key results (especially 3C-seq boundary calling) limits practical reuse. Machine-actionable reuse would typically involve a workflow specification (e.g., Snakemake/Nextflow) or containerized scripts with pinned versions and parameters. The reliance on a web tool for comparative genomics and the lack of released code for key custom computations reduce both findability and reusability of derived annotations. This matters for the field because replication and extension (e.g., across Streptomyces species/conditions) depend on being able to recompute compartments and boundaries consistently. The external quote therefore supports the criticism that the paper’s current computational packaging is insufficient for robust reuse and reproducibility.", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Gemini|1", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "The methodology described for identifying and replacing outliers in the 3C-seq contact maps is mathematically flawed and inappropriate for chromosomal contact data.\n\nThe contact score for a pair of bins that due to mapping was identified as an outlier (z-score>contact score) was replaced with the median value of the contact matrix.\nThis sentence describes a mathematically nonsensical comparison for outlier detection. A z-score is a standardized, dimensionless quantity (calculated as the number of standard deviations a value is from the mean), whereas a contact score represents a normalized frequency of interactions between genomic loci. Comparing a z-score directly to a contact score (i.e., z-score > contact score) is invalid because they exist on entirely different scales and have different units. This suggests a fundamental error in the implementation or description of the outlier removal algorithm.\nThe contact score for a pair of bins that due to mapping was identified as an outlier (z-score>contact score) was replaced with the median value of the contact matrix.\nFurthermore, replacing an outlier with the \"median value of the contact matrix\" is highly problematic for 3C-seq data. Contact matrices of chromosomes are characterized by a strong diagonal (representing high contact frequencies between adjacent loci) and sparse off-diagonal elements, meaning the global median of the matrix is typically close to zero or the background noise level. Replacing an outlier—especially one near the diagonal—with the global median would artificially introduce a \"hole\" in the contact map, disrupting the local interaction landscape and potentially skewing downstream analyses such as the identification of boundaries or domains. A more appropriate approach would be to replace outliers with the local median or interpolate from neighboring bins.\nRaw contact maps were normalized with the sequential component normalization procedure (SCN73). To facilitate visualization, contact matrices are visualized as log matrices.\nThe sequential component normalization (SCN) procedure is a standard method for normalizing Hi-C data [1]. However, the subsequent outlier removal step described by the authors undermines the integrity of the normalized data. The combination of a flawed outlier detection metric and an inappropriate replacement strategy casts doubt on the reliability of the resulting contact maps and any downstream structural analyses derived from them.\n\nReferences:\n[1] [Lieberman-Aiden, E., et al. (2009). Comprehensive mapping of long-range interactions reveals folding principles of the human genome. Science, 326(5950), 289-293.](https://doi.org/10.1126/science.1181369)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Gemini|2", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "The addition of a massive pseudocount (5% of the global maximum contact frequency) to all bins prior to log transformation severely distorts the contact map and dampens biologically meaningful long-range signals.\n\nHere, we also added pseudocounts (equal to m/20 where m is the maximal value of the contact frequencies) such that all values of the contact maps are strictly positive and we considered the logarithm of the resulting maps in order to mitigate the strongest variations close to the diagonal.\nAdding a pseudocount equal to m/20 (5% of the global maximum contact frequency) to all bins is an excessively large adjustment. In 3C-seq and Hi-C data, the maximum contact frequency m typically occurs on the main diagonal between adjacent bins and is orders of magnitude higher than off-diagonal, long-range interaction frequencies [2]. Adding 5% of this maximum value to the entire matrix will overwhelm the true signal in the off-diagonal regions, effectively washing out long-range contact patterns and domain structures.\nHere, we also added pseudocounts (equal to m/20 where m is the maximal value of the contact frequencies) such that all values of the contact maps are strictly positive and we considered the logarithm of the resulting maps in order to mitigate the strongest variations close to the diagonal.\nConsequently, when the logarithm is subsequently applied, the relative differences between biologically meaningful long-range contacts and background noise will be severely dampened (e.g., original values of 1 and 10 might become 51 and 60, reducing a 10-fold difference to a mere 1.17-fold difference before log transformation). This massive pseudocount likely distorts the data, making the Frontier Index heavily reliant only on the very strongest near-diagonal contacts and potentially missing weaker but biologically significant boundaries. Standard practice involves adding a minimal pseudocount (e.g., 1 or the minimum non-zero value) solely to avoid undefined values during log transformation [4].\n\nReferences:\n[2] [Dixon, J. R., et al. (2012). Topological domains in mammalian genomes identified by analysis of chromatin interactions. Nature, 485(7398), 376-380.](https://doi.org/10.1038/nature11082)\n[4] [Lioy, V. S., et al. (2018). Multiscale structuring of the E. coli chromosome by nucleoid-associated and condensin proteins. Cell, 172(4), 771-783.](https://doi.org/10.1016/j.cell.2017.12.027)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Gemini|3", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "The procedure used to normalize antisense-transcription data is mathematically ambiguous and potentially incorrect, raising concerns about the accuracy of antisense transcription quantification.\n\nTo ensure that antisense-transcription did not affect the normalization of sense-transcription data, the latter were normalized as follows: the percentage of transcription in antisense orientation of each gene was determined with the raw data, then the normalized antisense-transcription was evaluated by applying this percentage to the normalized sense-transcript counts.\nThis description of the normalization procedure for antisense transcripts is highly irregular and mathematically ambiguous. If \"percentage of transcription in antisense orientation\" is defined conventionally as raw_antisense / (raw_sense + raw_antisense), then multiplying this percentage by the normalized_sense counts does not yield the correctly normalized antisense counts (which should simply be raw_antisense / size_factor).\nTo ensure that antisense-transcription did not affect the normalization of sense-transcription data, the latter were normalized as follows: the percentage of transcription in antisense orientation of each gene was determined with the raw data, then the normalized antisense-transcription was evaluated by applying this percentage to the normalized sense-transcript counts.\nEven if the authors intended to calculate the ratio raw_antisense / raw_sense and multiply it by the normalized sense counts (which would mathematically equal raw_antisense / size_factor), describing this as a \"percentage\" applied to sense-transcript counts is confusing and non-standard. The standard and robust approach in RNA-seq analysis is to apply the library size factors (e.g., those estimated by DESeq2 from sense transcripts or total transcripts) directly to the raw antisense read counts [3]. The convoluted method described introduces unnecessary ambiguity and raises concerns about the accuracy of the antisense transcription quantification used in the study.\n\nReferences:\n[3] [Love, M. I., Huber, W., & Anders, S. (2014). Moderated estimation of fold change and dispersion for RNA-seq data with DESeq2. Genome biology, 15(12), 550.](https://doi.org/10.1186/s13059-014-0550-8)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Gemini|4", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "The strict requirement for both upstream and downstream peaks to define a boundary, and the subsequent exclusion of \"orphan\" peaks, may lead to the loss of biologically meaningful structural features in the chromosome.\n\nA boundary was then allocated to any bin (as well as to pairs of consecutive bins to cope with uncertainty of peak positions) for which both the upstream and downstream peaks were significant.\nThe authors define a chromosomal boundary strictly as a locus where both upstream and downstream peaks in the Frontier Index are significant. This stringent requirement assumes that all true boundaries must exhibit a symmetric or bidirectional effect on chromosomal contacts, which is not necessarily true for all biological insulators or structural features [5].\nNote that due to intrinsically noisy nature of 3C-seq data, we detected bins with only an upstream or a downstream significant peak (Supplementary Fig.3.D). These bins with an ‘orphan’ peak were not associated with a boundary, and hence, were removed from the analysis.\nDiscarding bins with only an upstream or downstream significant peak (termed \"orphan\" peaks) by solely attributing them to noise is problematic. In bacterial chromosomes, boundaries can be formed by highly transcribed genes or specific protein binding sites that may exert a directional or one-sided insulation effect, leading to asymmetric contact patterns. By removing these \"orphan\" peaks from the analysis, the authors potentially discard biologically meaningful structural features, which could bias their conclusions regarding the correlation between genetic compartmentalization and chromosome structure. A more rigorous approach would involve investigating the genetic context of these \"orphan\" peaks rather than discarding them outright.\n\nReferences:\n[5] [Szafran, M. J., et al. (2021). Spatial reorganization of the Streptomyces venezuelae linear chromosome during sporogenic development. Nature Communications, 12(1), 5222.](https://doi.org/10.1038/s41467-021-25461-2)", "reviewer_type": "ai", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_1|1", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "The mechanism of chromosome organization and remodeling during differentiation remains an important and fundamental problem. It was previously reported that Streptomyces genomes are compartmentalized into central regions and terminal regions (Choulet 2006), and genes in these regions are differentially expressed in various growth conditions (Karoonuthaisiri 2005, Jeong, 2016). Using 3C-seq, the authors found that the chromosome forms CIDs bounded by highly transcribed genes during exponential growth and the CIDs boundaries disappeared during development (which was essentially prolonged growth/stationary phase). This correlation of gene expression and CID boundaries were previously described in multiple bacterial species (Le 2013; Le 2016; Marbouty 2015; Lioy 2018; Bohm 2020, and more). Therefore, this manuscript confirms and extends previous findings but do not provide many new insights.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_1|2", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "If they focused on the mechanism and biological relevance of this the change, the authors could have increased the impact of the work.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_1|3", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "There are some very straight forward experiments to address these. For example, are ParB/parS Smc-ScpAB required for the inter-arm contacts?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_1|4", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Do cells have a higher level of these proteins during development?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_1|5", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Is the increased inter-arm contact a consequence of the reduced transcription at stationary phase, i.e. if transcription is inhibited during exponential phase, would inter-arm contact increase?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_1|6", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Does inter-arm contact have an impact on development, i.e. does losing inter-arm contact (in ParB/Smc mutants) have a negative effect on the development? Without these answers, this manuscript does not add much to the canon.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_1|7", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "“Remodeling” indicates an active mechanism. However, the change of chromosome organization observed here could be passive, i.e. a byproduct of changed transcription. Without identifying a factor that remodels the chromosome, the authors should tune this down.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_1|8", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Changing from “open” to “closed” conformation is an overstatement. In exponential phase (Fig 3A), there is a faint off-diagonal, so the chromosome is not really “open”, but is weakly closed.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_1|9", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Figure 4F is not supported by the data. In exponential phase, there is some inter-arm contact in the data that is missing in the model. After 48 h of growth, only the regions near the origins are weakly interacting and these interactions do not extend to the entire genome. The authors should make the inter-arm contact weaker and shorter, not the strong alignment of the entire arms.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_2|1", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Introduction/Results: The authors have chosen to do their work in Streptomyces ambofaciens. Although well-studied, this is not one of the canonical models in the field. Although this is of course not a problem, it would be good to describe in the introduction/beginning results why this model was chose and not for instance S. venezuelae or S. coelicolor, which are more commonly used in the field.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_2|2", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "The arms of both chromosomes are quite different in length. Can the authors perhaps further explain how the disappearance of synteny (as described in Fig. 1, lines 104-105) relates to the different arms?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_2|3", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "The use of Extended Data Figures and Supplementary Figures is confusing. I expect that this will be dealt with in the final version?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_2|4", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "The authors seem to have used a modified version of YEME as mentioned in lines 388-390 (please indicate this clearly, as normal YEME contains 34% sucrose). Also, this medium is difficult to consider as a really biological relevant medium. Specifically, the medium imposes dramatic osmotic stress on the cells. How does this influence the organisation of the chromosome? Perhaps the authors can comment a bit on this in the discussion?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_2|5", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "I am curious if the authors think whether the change in chromosome conformation also relates to the genomic instability that is often witnessed in streptomycetes. The reason I mention this is because the authors seem to suggest that the high level of transcription in the central part of the chromosome, flanked by the boundaries is perhaps less prone to recombination (lines 318-320). Does this also mean that the recombination events (and genomic instability in the chromosomal arms) occurs during early growth (because those arms are not active then)?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_2|6", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Line 29. Change to \"...chromosome structure of Streptomyces ambofaciens correlates with...\"", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_2|7", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Line 46. The authors use e.g. However, what other forms of differentiation are meant? I think the authors mean i.e.?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_2|8", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Lines 60-64. The authors could include some references to work from other labs that have demonstrated genomic rearrangements (although admittedly the cited lab is leading in this respect).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_2|9", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Line 83-84 Change to: ...the numerous available Streptomyces ....\"", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_2|10", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Line 85. Omit \"new\" (it may be new for Streptomyces, but it is commonly used in other systems)", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_2|11", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Line 115. Change \"shorten\" to \"referred to as\"", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_2|12", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Line 120. Change to \"terminal\" (not terminals)", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_2|13", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Line 138. remove \"by S. ambofaciens\"", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_2|14", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Line 395. What filters were used?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_2|15", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Line 428. “owing to its location within the TIRs”. This is not clear. Please rephrase", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_2|16", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Line 434. Change to “Identification of NAPSFs”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_2|17", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Line 448. 1e-10 31?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_2|18", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Line 452-458. Split into 2-3 sentences for clarity.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_2|19", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Line 802. Same legend than Figure 3?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_2|20", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Line 829. Change “under” to “in”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_2|21", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Line 830. Omit “although”", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_2|22", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Line 841. I guess ATB is antibiotic?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_2|23", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Fig. 1. “Diversity” is without capital", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_2|24", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Ext. Data Fig. 1. Why did the authors not include a 72h YEME sample? It seems that the halo size is quite a bit bigger than at 48 h in YEME.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_3|1", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "However, I am struggling to connect metabolic differentiation with the presented data. There is no metabolite data shown and strong activation of a single BGC appears somehow limited evidence for metabolic differentiation. The authors claim activation of 20 % of putative SMBGC genes during stationary phase but it remains unclear to which extend this relates to ‘real’ metabolic changes. To me, chromosomal re-arrangements are clearly correlated to growth phase but, with the current data provided, only to limited extend to metabolic output.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_3|2", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Furthermore, I see limited support presented here for a better understanding of BGC regulation. The authors provide two examples for an overlap between BGC location and boundary formation. Given that there seemingly are around 20 BGCs in the investigated species, the finding of just two boundary overlaps appears limited. One of the two examples shows very high expression and in the other example rather low expression. As such, it remains unclear how BGCs influence domain formation. The role of boundary formation in cluster regulation remains unclear as well (see specific question below).", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_3|3", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "As a pioneering study for Streptomyces genetics, the manuscript would be significantly strengthened if the authors could provide any type of confirmatory experiments to their 3Cseq chromosome architecture data. DNA-FISH is the gold standard in the community and appears feasible to present evidence for the different chromosomal condensation states in the tested conditions. If FISH prove to difficult to be carried out, it maybe possible to present locus specific 3C data. This would appear particularly useful for the Congocidin BGC.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_3|4", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Fig 2a is unclear. Does each line represent a gene?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_3|5", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "L 147 – expressed and/or regulated – unclear.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_3|6", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "L 163-176 – antisense transcription – could the authors please expand. It is unclear how to align the positive correlation of antisense to sense transcription with the highest antisense index at lowly expressed genes. The authors suggest a role a gene regulation based on the presented data but avoid to outline a brief mechanistic model.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_3|7", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Congocidin BGC – Could the authors comment more exactly on Congocidine BGC transcription levels and boundary location? Is the boundary located within an operon? Is it separating different operons? If the latter, are these operons showing some kind of differential expression?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_3|8", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Stambomycin BGC – if transcription is responsible for boundary formation alone why does a boundary form at a lowly expressed BGC?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_3|9", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "It may be useful to include a differential interaction analyses for the Hi-C maps obtained under different conditions.", "reviewer_type": "human", "label": "error", "error_type": "Misunderstanding", "label_origin": "expert+llm-filter"}
{"id": "prb|85|Human_3|10", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "BGCs can be found in both pro- and eukaryotes. It would be helpful to discuss the findings with respect to findings in eukaryotes. Similarly, a wider discussion of the observed correlations between chromosome architecture and transcriptional activity would be useful. E.g. Rowley et al. 2017 Mol Cell 67", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_3|11", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "L292-293. Comment not precise without corresponding metabolite data.", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_3|12", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "L313-314. Unclear how the authors back up this comment. This requires clarification. How do the authors define a transcriptional hub? Should this be similar to transcription factories?", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}
{"id": "prb|85|Human_3|13", "source": "prb", "split": "test", "paper_id": "prb85", "comment": "Furthermore, this concept is supported to only limited extend as (i) these boundaries also form in areas without high transcriptional activity and (ii) the boundaries are lost in the central area in exponential phase even though loss of transcriptional activity is very limited according to the presented data. Conformational data on any mutant with reduced transcriptional activity or additional experimental support via e.g. HiChIP or standard ChIP against a bacterial polymerase would significantly enhance these claims. Ref: Nature Communications manuscript NCOMMS-21-01376-T", "reviewer_type": "human", "label": "correct", "error_type": null, "label_origin": "expert"}