1 Executive recommendation

Keep DraftMark’s existing RoBERTa release as the control. Build the next model around generalization to unseen rewrites, careful treatment of AI-assisted human writing, and low false-positive rates measured on the exact local artifact. A useful first comparison is a 68M/150M encoder student against the existing 125M model and an Ettin-1B teacher. Begin with English; add a dedicated Thai-English study as a second research track, using a multilingual backbone and locally collected evidence.

The most relevant compact competitor found in this review is GPTTrace Ettin-150M v5e. Its official RAID submission reaches 98.91% TPR at 1% FPR and 99.80% TPR at 5% FPR, including attacks. The updated Ettin-1B v8s submission reaches 99.54% and 99.93%, respectively. A browser implementation, INT8 weights, and teacher distillation already exist for the 150M competitor. Those features alone do not constitute a new research contribution. (RAID evaluation maintainers 2026a, 2026b; Nakas 2026a)

The more promising question is whether a small exported detector can preserve useful recall on unfamiliar rewriting processes while keeping human false flags low across populations and devices. This is both practically meaningful and less saturated than an aggregate RAID score. This report defines the comparisons and provides a training/evaluation starter package; it does not report a new H100 training run or new detector benchmark measurements.

1.1 Decisions at a glance

2 Scope and evidence protocol

This is a targeted critical review, not a systematic claim of exhaustive coverage. The search cutoff is 9 November 2026, Asia/Bangkok. The seed is saksornr/draftmark-roberta-int8. The review followed its base model, training notes, benchmark dependencies, and nearby detector literature, then checked recent official benchmark submissions and primary papers.

Search lanes included the seed/model provenance; references from RAID, MAGE, DetectRL-X, MELD and WATTLE; later leaderboard updates; multilingual and mixed-authorship benchmarks; larger likelihood/representation detectors; and official runtime documentation. Searches included combinations of AI-generated text detection, local, browser, INT8, paraphrase, low false-positive rate, Thai, multilingual, calibration, and H100. Author cards were treated as author reports, not independent replications.

Four evidence classes are used throughout:

1. Release evidence: DraftMark’s public manifests and aggregate report. These were inspected, not independently rerun.
2. Official benchmark evidence: RAID CI results at a pinned repository revision and organizer leaderboards.
3. Paper or author-harness evidence: exact reported datasets, splits and metrics, with their limitations retained.
4. Proposed experiment or target: an engineering/research decision in this report, not an achieved result.

The DraftMark main revision inspected was 068ccc7ba34f134526c9bbc72ac2033f00a40d45. The RAID snapshot was ac4ce10fe8fe096b0c4a01396f1e437aaf35bd53, dated 5 November 2026. The companion evidence files preserve exact scores, source URLs and versions. Public artifacts do not include DraftMark’s complete trainer, row-level evaluation predictions or full split manifests, so an independent reproduction of its original run is not yet possible from the release alone. (DraftMark project 2026b, 2026c, 2026a; Dugan et al. 2026)

3 What DraftMark already achieves

3.1 Model and deployment audit

DraftMark v3 is a fine-tuned RoBERTa-base detector, approximately 125M total parameters, initialized from Oxidane’s TMR checkpoint. It updates the last four encoder layers plus the classifier: 28,943,618 trainable parameters. The published training run used Apple MPS, 6,339 training drafts, 761 calibration/development drafts and 1,120 holdout drafts. The deployed model and tokenizer occupy 131,110,132 bytes, approximately 131.1 MB. (DraftMark project 2026b, 2026c; Oxidane 2025)

The release is English-only. It accepts 150-2,000 words, with a 20,000-character cap. The worker scores sentence-aligned windows of up to 512 tokens and aggregates AI scores by content-token count. The label order is human, then AI. Its production flag threshold is approximately 0.9991466, with a lower limited-signal cutoff of 0.25. These are product policies fitted for this artifact; 0.9991466 is not a calibrated 99.9% probability of authorship. (DraftMark project 2026b)

3.2 Published holdout: meaningful progress with an explicit tradeoff

These are the release’s own matched holdout results at each shipped policy, not a comparison with today’s best public Ettin checkpoint on an official leaderboard. Its paired 95% interval for mean rewrite improvement is +10.7 to +22.0 percentage points. The improvement is substantial on this sample, but the seq2seq regression is equally real. (DraftMark project 2026c)

3.2.1 What the aggregate numbers do not establish

First, zero learner false flags on 220 essays is not proof of a zero or sub-1% population error rate. The release’s two-sided Wilson upper bound is 1.72%. For 1/300 general-human false flags, the interval is approximately 0.059%-1.864%. A stronger low-FPR claim needs more independent human source groups.

Second, the release separately reports decoder AUROC 98.51% and seq2seq AUROC 98.27%, with diagnostic ROC recall around 74.50% and 76.51% at 1% FPR. These diagnostic values exclude out-of-input-limit cases and use ROC operating points. They must not replace the actual shipped recalls of 59.33% and 73.33%, whose denominators include the full cohorts. High ranking quality and a conservative production threshold can coexist.

Third, the latency result is 1.262 seconds p95 for a warm 300-word scan on an Apple M4 Pro in Chromium, based on 20 samples. It does not establish mobile latency, peak RAM, energy, or a complete offline cold-start experience. (DraftMark project 2026c)

The base TMR model was trained on RAID. DraftMark additionally used DetectRL-X-derived material and other sources. Its release documents overlap screening, including exclusions against public training sources, but acknowledges that unpublished upstream training data cannot be checked. Treat RAID as an important benchmark-distribution test and use fresh generators, rewriting methods and sources for genuine transfer claims. (Oxidane 2025; DraftMark project 2026c)

4 Benchmarks and exact scores to challenge

4.1 Official RAID: the public English benchmark gate

The following rows are from the same pinned official RAID snapshot, all settings including attacks, covering 672,000 test IDs. Scores are percentages. These are selected relevant competitors, not a claim that every model is publicly runnable at the same precision. (Dugan et al. 2026; RAID evaluation maintainers 2026a, 2026b; C. Li, Wan, and Paetzold 2026)

Practical interpretation: a comparable compact detector must challenge 98.91% TPR at 1% FPR, while 99.54% is the relevant verified open 1B reference. A universal leaderboard claim must also address the strongest closed submissions. Beating legacy OpenAI GPT-2 RoBERTa detectors would not establish modern state of the art.

The newer v8s result supersedes older pages quoting 99.42% TPR at 1% FPR for the 1B model. Avoid copying stale ranks: an October 31 submission also changed the ordering after GPTTrace’s October marketing table. The exact unrounded metrics are preserved in the evidence CSV. (RAID evaluation maintainers 2026b; Dugan et al. 2026)

4.1.1 A critical threshold distinction

The official evaluator defaults to per-domain tuning. It chooses each domain’s threshold using unattacked human test scores, then applies that threshold to AI text and pools the resulting counts. This is the official diagnostic protocol; it is not evidence that one fixed threshold calibrated earlier will maintain 1% FPR for unknown app users. The paper should report both official RAID numbers and a second deployment track with independent calibration. (Dugan et al. 2026)

Also, the 150M competitor’s card reports a small-sample INT8 versus PyTorch discrepancy: AUROC 0.975 versus 0.990 on 300 MAGE texts. Its official RAID number should not automatically be attributed to the exact deployed INT8 browser artifact. Re-evaluate that artifact under the same runtime and input policy as DraftMark. (Nakas 2026a)

4.2 MAGE: generation and paraphrase transfer

MAGE supplies explicit OOD generator and paraphrase testbeds. Useful author-reported reference points are below. They are not a centralized current SOTA ranking; reproduce the exact testbed and scoring pipeline before asserting a win. (Y. Li et al. 2024; Nakas 2026a, 2026b)

DivEye separately reports 0.87 paraphrase AUROC, and its combination with BiScope reports 0.89. These establish that 0.756 is a useful direct compact-competitor baseline, not the best score in the literature. (Basani and Chen 2026)

Label policy matters. MAGE’s original labels use 0 for machine and 1 for human. Its paraphrase testbed includes machine-rewritten human text under the machine-generated category. Preserve that definition for official comparability, then separately measure human-origin writing with light AI assistance. A product that intends to protect human-origin writing is answering a different question from detecting any machine intervention. (Y. Li et al. 2024)

4.3 DetectRL-X: multilingual and editing-sensitive evaluation

DetectRL-X evaluates binary and ternary detection over eight transfer dimensions. Its languages do not include Thai. The table below reproduces its Table 2 averages. The column labeled macro-F1 at 1% FPR reports F1, not true-positive rate. (Wu et al. 2026)

The cross-paraphrase binary slice is much harder: XLM-R reaches 77.32 best macro-F1 and 64.13 macro-F1 at 1% FPR. For the ternary task, mDeBERTa’s macro-F1 at 1% FPR is 81.10. These are useful challenge scores. Larger decoder-based systems do not automatically win, but the encoder systems receive supervised training: this is not a controlled estimate of model-size effects. (Wu et al. 2026)

Because DraftMark already draws from DetectRL-X, evaluate only documented held-out groups for regression and reserve genuinely unseen generator/rewriter/source combinations for transfer. Do not call the complete dataset unseen merely because a particular test file was not used.

4.4 WATTLE: a harder test of web rewriting

WATTLE is a recent source-matched web benchmark. Its results make the research gap clear: good conventional benchmark scores coexist with poor detection at fixed low-FPR operating points. Table 4 reports the following spin/rewrite results; each method uses its own calibrated operating point. (Chernikov, Ptitsyn, and Burlova 2026)

A useful experiment should challenge the strongest relevant baseline on each metric, not only the proposed method in the paper. On this comparison, surpassing PAWN++’s 58.1 frontier AUROC is insufficient because RADAR already scores 75.4. Re-run current GPTTrace and MELD/Vanguard comparators here before describing a new result as the best available. The paper’s clean RAID-train results are a separate protocol and are deliberately omitted from the official RAID table. (Chernikov, Ptitsyn, and Burlova 2026)

4.5 Shared tasks and supporting benchmarks

PAN-CLEF 2026 provides an adversarial software-submission setting. The winning system’s composite score is 0.975, with F1 0.976 and FPR 5.3%; the second-place ModernBERT system has AUROC 0.993 but FPR 10.8% at its submitted decision rule. Its ranking is a composite, not a low-FPR guarantee. The task’s data page restricts redistribution and commercial reuse; use it within its stated research terms. (PAN organizers 2026)

COLING 2025’s GenAI detection shared task offers additional transfer checks: 83.07 English test macro-F1 and 79.16 multilingual test macro-F1 are organizer-reported winning scores. These are distinct from development accuracy. MULTITuDE is useful for broader cross-language diagnosis but does not include Thai. Legacy HC3, Ghostbuster and original DetectRL are supporting tests, not sufficient evidence of current frontier robustness. (Wang et al. 2025; Macko et al. 2023)

5 Model strategy: small students, relevant larger comparators

5.1 Recommended model ladder

Ettin exposes 17M, 32M, 68M, 150M, 400M and 1B encoder scales. Begin with 68M and 150M rather than running the entire ladder. Microsoft’s mDeBERTa card counts 86M backbone plus about 190M embedding parameters, approximately 276M total, not 86M. Its multilingual pretraining and Thai evaluation make it a reasonable Thai starting point, but they do not establish Thai AI-detection accuracy. (JHU CLSP 2025; Microsoft 2021)

MELD’s paper describes a 396M trainable Ettin-400M configuration. Its current model repository differs, so compare a pinned paper-era artifact or explicitly label a fresh reproduction. Vanguard reports 0.9475 mean OOD AUROC across seven datasets, but this author-harness mean cannot be ranked against RAID or DetectRL-X aggregates. (C. Li, Wan, and Paetzold 2026; Thorat 2026)

5.2 How to compare larger models fairly

Use two experiments. In the released-system comparison, run each published detector using its documented preprocessing, then fit operating thresholds on the same permitted calibration population. In the controlled architecture comparison, train the selected student and larger encoder on the same groups, labels, sampling distribution and tuning budget. Report both; they answer different questions.

For a decoder comparator, specify the exact observer/scoring pair, dtype, sequence limit and feature extraction. Binoculars uses paired model likelihoods; Fast-DetectGPT’s maintained repository recommends newer model pairs than its original experiment. Count all resident models and inference passes, not only the learned classification head. A 2.7M head atop two frozen 1B probes is still roughly a 2B inference system. (Hans et al. 2024; Bao et al. 2026; Chernikov, Ptitsyn, and Burlova 2026)

Do not compare H100 latency for a large model with phone CPU latency for the student as though the hardware were matched. Report server throughput separately from device batch-one latency. For each target device, list either measured performance or the concrete reason a model cannot run under the selected memory/runtime budget.

6 Improvements most likely to matter

6.1 Prioritize data coverage before architecture novelty

The present failure pattern suggests a targeted first intervention: expand decoder-style rewriting while retaining enough seq2seq examples and difficult human negatives to avoid another recall tradeoff. Start with a controlled 50k-100k-example experiment, then test 200k-300k only if the held-out transfer curve justifies it. Those counts are proposed experiment sizes, not requirements or demonstrated optima.

Create matched groups containing the original human source, independent AI drafts on the same topic, multiple rewrite styles and any subsequent edits. Hold out entire source families, generator families and rewriting methods in separate test tracks. Match length, topic and formatting across classes so the classifier cannot solve the task by recognizing different corpora.

Human negatives should include learner prose, formal technical writing, templated business text, short but valid passages, translated writing and repeated-domain vocabulary. Recruit or license a distinct learner-writing corpus for final evaluation. Reusing ASAP-derived patterns in both development and the only learner test gives a narrow estimate of real-world fairness.

Keep the current v3 holdout as a regression suite. Once its results guide multiple decisions, it is no longer an untouched final test. Repeatedly changing thresholds or examples based on that holdout would make later headline gains less convincing.

6.2 Treat editing provenance explicitly

Use four documented provenance groups: human originals; human-origin drafts lightly edited by AI; AI-origin drafts rewritten or human-edited; and unedited AI drafts. Where available, retain edit operations and aligned spans. Derive benchmark labels from each benchmark’s stated definition rather than forcing one universal label mapping.

For product evaluation, separate origin from assistance. A detector may recognize machine polishing without establishing that the underlying ideas or draft came from AI. A third assisted/uncertain outcome can be useful, but only when trained and evaluated with those labels. Document-level supervision alone does not justify presenting sentence highlights as verified machine-authored spans.

This construct distinction is central to the proposed publication. It prevents a model from appearing more robust simply because it flags all polished human writing as AI.

6.3 Distillation is useful engineering, not sufficient novelty

After measuring the English teacher on training/development groups, train a compact student with hard labels and cached teacher logits. A reasonable starting objective is:

$$\mathcal{L}_{\mathrm{base}}=(1-\alpha)\,\mathrm{CE}(y,p_s) +\alpha T^2\,\mathrm{KL}(p_t^{(T)}\,\|\,p_s^{(T)}).$$

Try $T=2$ and a small grid for $\alpha$, selected only on development data. Preserve hard provenance labels when a teacher is confidently wrong. Cache logits with model revision, tokenizer, text checksum and class mapping. Teacher use of test data is still training contamination after distillation.

Then ablate one extra mechanism at a time: clean/rewrite consistency for transformations that preserve the task label; ranking against hard human negatives; and group-balanced sampling or group-aware validation. MELD already combines auxiliary heads, an EMA consistency teacher and hard-negative ranking. Reproducing those components is a strong baseline, not a new method claim. (C. Li, Wan, and Paetzold 2026)

6.4 Research candidate: stability of the human-score tail after export

The proposed method-level question is whether training and calibration designed around the exported score distribution improve low-FPR transfer more than ordinary distillation plus post-training quantization.

Evaluate FP32/BF16, weight-only INT8, and any candidate activation-quantized version on identical calibration and test groups. Track the change in human-tail quantiles, decision flips, worst-group FPR and rewrite recall. If export hurts tail separation, investigate a quantization-aware consistency term or selective higher precision for sensitive layers, keeping training data and tuning budgets matched.

This is a hypothesis to test, not an established first. A negative result is informative: post-export calibration alone may be sufficient, or a different student architecture may be more effective. Quantization is not lossless, and runtime documentation explicitly recommends inspecting where numerical changes arise. (ONNX Runtime contributors 2026c)

Temperature scaling can improve probability calibration on a matching population; it cannot create missing class separation or guarantee FPR under distribution shift. Use it as a calibration baseline, not as the central explanation for OOD gains.

7 Evaluation protocol for a publishable result

7.1 Separate four roles for data

Maintain distinct training, model-selection development, threshold calibration, and final test partitions. Split before augmentation, grouping originals, descendants, near duplicates and author/source families when available. Keep generator/rewriter holdouts distinct from ordinary random source-group splits.

Each row should include a stable ID, source-group ID, text checksum, language, domain, provenance label, generator and revision, edit method, generation date, source/license information and split. Manifest joins must require a prediction or an explicit invalid result for every expected ID. Missing outputs must not silently improve recall or false-positive estimates.

Report training-data exposure for every released comparator. A teacher or baseline may have seen benchmark training sources or unavailable private data. Separate verified disjoint tests from tests where exposure is unknown; do not claim that one model’s data advantage demonstrates an architectural advantage.

7.2 Primary metrics

The main deployment table should report, per dataset and subgroup:

• TPR/recall at the calibration-selected fixed threshold and the actual test FPR.
• Human false-flag counts, denominators and 95% confidence intervals.
• AUROC and partial AUROC over the low-FPR region as threshold-independent diagnostics.
• Precision at declared base rates, not only the balanced test-set precision.
• Abstention/unsupported-input rates and risk-versus-coverage curves.
• Model bytes, peak runtime memory, cold/warm p50/p95 latency and supported runtime/device.

If 1% of checked documents are actually AI-origin, a detector with 90% recall and 1% FPR has illustrative positive predictive value:

$$\frac{0.90\times0.01}{0.90\times0.01+0.01\times0.99}=47.6\%.$$

This is a base-rate calculation, not a measured DraftMark deployment result. It explains why a seemingly small FPR still matters for a writing tool.

7.3 Calibration and statistical uncertainty

Select a threshold on calibration human scores, with a documented strict/non-strict tie rule. Freeze it before test evaluation. For multiple supported populations, predeclare whether the policy uses one global threshold or observable language/length buckets. Do not silently select a more favorable threshold after observing a test domain.

For initial development, collect several thousand independent human source groups. For a credible 1% deployment claim, aim for roughly 10,000 human examples per priority population where practical, reporting both sample and independent-group counts. At a true 1% rate, a simple independent-binomial standard error with 10,000 cases is about 0.10 percentage points; correlated documents reduce effective information. For a 0.1% target, the necessary human test scale is substantially larger.

Zero events provide a useful sanity check: the approximate one-sided 95% rule-of-three upper bound is $3/n$. With 220 essays, that is about 1.36%; the two-sided Wilson interval used by the release is wider. State the interval convention rather than mixing bounds.

Use paired source-group bootstrap intervals for differences between models on the same examples. Report seed variation separately from test sampling uncertainty. Frozen-calibrator test bootstrap intervals are conditional on the chosen threshold; if making a stronger claim about calibration stability, also resample the calibration groups and refit thresholds. When many subgroup constraints are asserted simultaneously, account for multiple comparisons or label intervals as exploratory.

7.4 Concrete success criteria, defined before the next test

8 H100 training plan

8.1 Start on one GPU

The current 125M detector is small enough that a single H100 is the appropriate first allocation. Training with BF16 autocast while retaining FP32 optimizer states is a straightforward starting point. A rough full-Adam parameter-state budget of 16 bytes per parameter implies about 2 GB for 125M parameters and 16 GB for 1B, before activations, temporary buffers and framework overhead. These are arithmetic memory estimates, not measured allocations; the exact software stack and batch/sequence sizes determine actual usage. (PyTorch contributors 2026)

Do not begin by distributing the original 6,339-example experiment across four H100s. First establish correctness and throughput on one. Multi-GPU training becomes useful for larger data, teacher sweeps or long sequences after profiling.

8.2 Run sequence

The original published recipe is last four layers plus classifier, 384-token training cap, global batch 16, AdamW learning rate $2\times10^{-5}$, weight decay 0.01, clipping 1.0, three epochs and seed 36513. Its cohort weights are learner 1.45, decoder 1.30, seq2seq 0.90 and encoder 1.0. Match these first; increasing batch size is a new experiment, not a transparent acceleration. (DraftMark project 2026a)

For the expanded-data run, profile sequence lengths and try a small development-only grid: learning rates $1,2,4\times10^{-5}$, 384/512 tokens, and one to three epochs. Use microbatches and accumulation to reach a specified effective batch without changing it accidentally. Record all decisions before final-test access.

8.3 Warm-start reconstruction

The public training branch contains replacement tensors for the trained layers. They must replace the corresponding tensors in the pinned TMR base, not be added as a LoRA delta. Validate the expected key set, label order, parameter count and SHA-256, then initialize a new optimizer for continued training. The supplied training kit implements this reconstruction and a new single-GPU entry point. It is not the unpublished original trainer and cannot promise bitwise reproduction. (DraftMark project 2026a)

The kit supports source-grouped local JSONL inputs, weighted loss, optional cached teacher logits, checkpointing/resume and run provenance. The separate evaluator operates on prediction files from the actual deployment runtime, so native training validation cannot accidentally substitute for exported-browser evaluation.

8.4 Estimate time from a pilot

Measure examples/second and tokens/second after warm-up on the intended batch and sequence distribution. Estimate training time as:

$$t_{\mathrm{hours}}\approx\frac{N_{\mathrm{examples}}\,E}{3600\,r_{\mathrm{examples/sec}}}+t_{\mathrm{evaluation}}+t_{\mathrm{export}}.$$

For illustration only, 300,000 examples across three epochs at 50 examples/second would require five hours of training computation before evaluation/export. The throughput is a hypothetical input, not an H100 benchmark. Teacher scoring, dataset generation and repeated app evaluation may dominate the overall research schedule. Avoid committing to an H100-hour budget until the pilot is measured.

9 Local app development

9.1 Build on the existing browser product

DraftMark already has a local browser application. The next app milestone should make the model lifecycle and offline behavior reliable: package the runtime, tokenizer, model and decision policy under versioned hashes; cache them; verify a full reload and scan in airplane mode after installation; and keep processing off the UI thread. Downloading assets once is compatible with local inference, but it is different from working offline before the first installation. (DraftMark project 2026b; ONNX Runtime contributors 2026b)

Keep the existing weight-only INT8 path as the compatibility baseline. The handoff states that activation-quantized trials produced browser/native score drift. Do not replace it with generic dynamic quantization just because another model uses that format. After any export or runtime change, refit calibration on the shipped graph and inspect threshold flips, especially among high-scoring human texts. (DraftMark project 2026a; ONNX Runtime contributors 2026c)

ONNX Runtime Web can use WASM and other execution providers. Multithreaded WASM requires the browser’s support and cross-origin isolation. WebGPU should be an optional measured backend, with operator compatibility and parity verified, rather than a promised speedup. Runtime-native mobile providers also have device-specific behavior and may fall back or partition graphs. (ONNX Runtime contributors 2026d, 2026a)

9.2 App rollout sequence

The minimal user flow is paste/import, check locally, and review a cautious evidence result. Use states such as strong AI-like signal, inconclusive and outside the supported range. A detector score is not proof of misconduct. Show model version and supported-language/length information where useful; do not present an uncalibrated softmax as an authorship percentage.

Measure at least short, medium and long supported drafts. Report download/install separately from cold model load and warm inference, plus UI responsiveness, batch-one latency, peak RAM and repeated-scan thermal behavior. Model file size alone is not RAM usage. On-device optimization should minimize cost at matched error rates; a smaller graph that sharply increases learner false flags is not a successful product optimization. (ONNX Runtime contributors 2026a)

10 A focused Thai-English research extension

This extension fits a multilingual research program, but it should not delay the first rigorous English release. DetectRL-X and MULTITuDE leave Thai outside their language sets. That is a coverage gap in those benchmarks, not proof that no Thai detector or dataset exists. (Wu et al. 2026; Macko et al. 2023)

Start from a Thai-capable multilingual teacher. Build a provenance-controlled paired set with Thai originals, English originals and naturally code-switched text. Include locally written academic, professional and everyday prose; translated text; Thai speakers’ English; grammar assistance; heavier rewriting; and mixed human/AI drafts. Preserve authors, sources and rewriting lineage across splits.

Thai should not use an English whitespace word-count gate. Specify character or tokenizer-based length buckets and audit tokenization efficiency, sentence segmentation, Unicode normalization and code switching. Avoid normalizers that erase meaningful Thai marks. Test whether a compact shared student, separate language models, or a language-routed design gives the best quality/memory tradeoff. Calibration buckets must be based on observable supported language information and tested under code switching.

A useful publication claim would be: a provenance-controlled evaluation of compact local detectors under Thai-English editing and generator shift, with uncertainty and device cost measured together. Claiming the first Thai AI detector would require a dedicated novelty search beyond this review.

11 Report and publication strategy

11.1 What can be published now

The current public model supports a transparent engineering report: its training provenance, exact shipped artifact, cohort-level regression results, confidence intervals and reference-device latency. The report should acknowledge the seq2seq recall loss and limited human-test scale. Its defensible claim is improved performance over the previous DraftMark policy on that holdout, not state of the art across AI-text detection. (DraftMark project 2026c)

This document can accompany that release as a research roadmap and benchmark audit. It intentionally distinguishes reported evidence from experiments still to run.

11.2 What would justify a stronger paper

Frame the next paper around one main hypothesis: quantized compact encoders can retain useful low-FPR generalization under unseen rewriting and editing while reducing device cost relative to larger detectors. A bilingual extension can test whether this survives under language and code-switching shifts.

The minimum convincing experiment set is:

1. A matched comparison of current released detectors on public testbeds and a fresh untouched transfer test.
2. A same-data student/teacher study separating architecture, additional data and distillation effects.
3. Ablations of rewrite balancing, hard human negatives and the proposed export-aware method.
4. Calibration on separate data, with subgroup FPR counts/intervals and a clearly defined abstention policy.
5. Native-versus-exported quality, browser/device latency and peak-memory measurements using identical documents.
6. Transparent limitations, source-exposure audit, task-label mappings, and enough manifests/predictions to reproduce the findings where licenses allow.

Report paired intervals for the principal improvements and three training seeds for the final selected recipe when feasible. Choose the primary benchmark and metric before searching many variants. A 0.1-point gain on a saturated aggregate with a weaker human-error tail is not the intended success.

Potential formats include a technical report first, then an NLP system-demonstration or applied/industry paper if deployment is the main contribution, or a methods/benchmark paper if transfer and the Thai-English study provide substantial new evidence. Venue eligibility, deadlines and disclosure requirements must be checked when a submission is selected; none is assumed here.

11.3 Suggested paper outline

Use an introduction grounded in real local-writing use cases, followed by task/provenance definitions, related work, data/splits, method, calibration protocol, main comparisons, quantization/device analysis and error analysis. The main results table should include both quality and measured cost. Place exact benchmark adapters, prompts, source licensing and checkpoint/runtime hashes in the appendix and repository.

The release package should contain model weights, tokenizer, label mapping, runtime/policy versions, calibration provenance, a benchmark table with evidence status, reproducible commands and device results. Where raw text cannot be redistributed, release permitted IDs/hashes and reconstruction instructions instead of pretending an aggregate JSON alone is fully reproducible.

12 Prioritized execution plan

First, reproduce the current product’s behavior and establish the comparison harness. Recover the original source checkout and dataset manifests; restore the pinned model; generate browser-runtime predictions; rerun the compact and 1B competitors on the same independent calibration/test sets. This determines whether the biggest deficit is model separation, threshold transfer, input handling or the chosen text populations.

Second, run the one-H100 controlled adaptation. Expand decoder rewrites and difficult human negatives, retain seq2seq coverage, compare partial/full unfreezing, and evaluate with a fresh final set. Only advance to a new encoder after the data and calibration baselines are understood.

Third, train the compact student and validate the export. Distill into 150M/68M candidates, compare export formats, freeze calibration, and measure on the target desktop and mobile devices. Use these results to decide which model belongs in each local tier.

Fourth, publish the verified result and extend the study. Release the English evidence and app update when the gates are met. Develop the Thai-English provenance-controlled benchmark as a distinct research contribution, keeping the public paper’s claims tied to the actual measured populations and devices.

13 References