First, the commentators state that we “cite no clinical evidence for the use of 95 ng/mL or for an association between that threshold and the probability of relapse for AL”.

We modeled the link between aripiprazole plasma concentrations, which are generated through the respective PK models for AL [3] and AM [4], and relapses using an exposure–response relationship (PD model).

As no exposure–response relationships for aripiprazole have been published based on AL clinical trials, we used the only published relationship between aripiprazole plasma concentrations and relapses (Wang et al. [ 4]), which was based on AM studies.

Further, in their argument that “no exposure-response relationship has been observed for oral aripiprazole or for AL”, the commentators cite two published meta-analyses of a dose response of antipsychotic drugs [5, 6].

However, failure to establish a dose response does not preclude establishing a relationship between pharmacokinetics-pharmacodynamics, especially as the latter takes into account differences in drug plasma concentrations between individuals receiving the same dose.


In addition, as both AM and AL exert their action via the common active aripiprazole, it is plausible to assume the same aripiprazole exposure–response relationship for both formulations.

The difference between the long-acting injectable formulations is not in the pharmacodynamics but in the pharmacokinetics of the two formulations (i.e., the different PK profiles), as mentioned by the commentators [1].

We account for those differences between the formulations in the PK part of our PK–PD–PE analysis.


Second, the selection of an exponential survival model with the 95-ng/mL concentration threshold by Wang et al. [ 4] was informed by observed clinical trial data.

The exposure–response analysis initially evaluated aripiprazole minimum plasma concentration (Cmin) as a continuous variable; however, the model resulted in a misfit at Cmin > 95 ng/mL (i.e., the model predicted increasing Cmin was associated with a longer time to relapse at Cmin > 95 ng/mL), whereas the observed data showed a similar time to relapse in this exposure range.

As a result, an exponential survival model with the 95-ng/mL concentration threshold was evaluated and the results showed that the model prediction agreed reasonably well with the observed data.

Therefore, the model was considered sufficiently robust to predict the probability of relapse in patients with schizophrenia based on aripiprazole Cmin.

Of note, a recently published article [7] supports the conclusions of Wang et al. [ 4], proposing a minimum aripiprazole therapeutic reference range of 120 ng/mL regardless of the formulation.


Third, the commentators [1] question the use of a dichotomous hazard function for Cmin.

As explained above, the use of this hazard function is validated against observed clinical trial data and considered robust to predict the probability of relapse.

In addition, as mentioned in the article, we tested the impact of a continuous hazard function on the model outcomes and found a decrease in the number of relapses and total costs for all regimens, resulting in increased incremental costs per relapse avoided in most comparisons.

However, using a continuous hazard function does not change the conclusions of our study.


Last, the commentators raised two points pertaining to dosing regimens used in practice and our analysis.

The first relates to our statement regarding the use of AL 441 mg.

While we acknowledge that the AL 441 mg dose may be used for all persons taking AL (not just those who cannot tolerate higher doses), it remains true that this dose is used less often in clinical practice (based on IQVIA prescription data) and may be used in those patients who cannot be prescribed higher doses as per the prescribing information, which advises to adjust the AL dose as needed [8].

The second relates to the inclusion of the AL 1064 mg every 6 weeks regimen in our analysis.

Early dosing of AL may be considered as per the prescribing information [8], and IQVIA prescription data suggest this regimen is being used in clinical practice in the USA.

Again, in the absence of efficacy data regarding this dose, we felt the need to include it in our analysis to provide decision makers with cost-effectiveness information.

We reject the statement that conclusions regarding this dose are not meaningful; there is no reason to assume the PK profile of 1064 mg every 6 weeks cannot be estimated using the same population PK model as used for other AL regimens [3].


In summary, in the absence of comparative clinical evidence of AM versus AL, we developed a novel PK–PD–PE model to conduct a pharmacoeconomic evaluation of aripiprazole long-acting injectable regimens in schizophrenia in the USA.

As expressly stated in our article, the results of our analysis are subject to uncertainty and rely on assumptions, but we used the best-available peer-reviewed evidence for the PK and PD inputs.

Therefore, we remain with our conclusion that a PK–PD–PE modeling framework can be used to help to inform clinical and payer decisions in the absence of clinical trial data in a post-marketing setting.


Thank you again for the opportunity to respond to this letter.


This article is protected by copyright.

All rights reserved.


How to accurately and precisely measure animal density (i.e., the number of animals per unit area) is a long-standing but not fully resolved question (Dénes, Silveira & Beissinger 2015).

With the recent technological achievements in wildlife video recording, managers and ecologists have gained powerful tools for improving terrestrial and aquatic wildlife surveys, which typically target animal distribution, abundance or behaviour (Burton et al. 2015).

For example, unmanned aerial vehicles (UAVs) are currently used for a wide range of wildlife monitoring applications (Linchant et al. 2015), covering birds (Vas et al. 2015) to terrestrial and aquatic mammals (Martin et al. 2012; Hodgson et al. 2016).

In aquatic systems, the recent miniaturization and cost reduction of underwater video recording devices and the installation of cabled video observatories have broadened the remote, long-term and high-frequency monitoring of fish and their environments (Aguzzi et al., 2015; Matabos et al. 2015).

An additional advantage of camera devices is the minimization of wildlife disturbance (Assis et al. 2013; Vas et al. 2015) and researcher risk linked to surveying under difficult conditions and in hard-to-reach populations or areas (Martin et al. 2012; Hodgson et al. 2016; Goebel et al. 2015).

Overall, changing from conventional survey methods (e.g., physical mark-and-recapture surveys, visual censuses, trammel-net surveys, etc.) to camera-based wildlife assessment may represent a paradigm change in the current technological era.


For example, photo- identification (Moya et al. 2015) may become the input for spatial capture-recapture models (Chandler & Royle 2013).

Concerning marine wildlife assessment, conventional methods (e.g., underwater visual census) are currently being complemented with data from underwater cameras (see Mallet and Pelletier (2014) for a review).


The technological advances in wildlife imaging have opened at least two new challenges and opportunities: developing novel algorithms for data mining and automated image interpretation (Aguzzi et al. 2015, Boom et al. 2014, Díaz-Gil et al. 2017; reviewed in Dell et al. 2014) and fostering theoretical links between the patterns depicted by cameras and absolute animal density.


Here, we focus on this second challenge because there continues to be debate on which method and camera metric should be preferred.


Most of the proposed methods can be classified into two broad categories: empirical approaches that aim to correlate a given camera metric with independent estimates of density (e.g., Pelletier et al. 2011; Bacheler et al. 2013; Schobernd et al. 2014; Campbell et al. 2015) and theoretical approaches that exploit different model-derived expectations regarding how animals move


Several mechanistic models are able to reproduce the spatial patterns displayed by free-ranging animals, which consist of remaining within a relatively small area or HR most of the time (Börger et al. 2008; Van Moorter et al. 2009).

Among them, for simplicity and convenience, we considered the biased random walk (BRW), which can be mathematically described as a special case of the Langevin equation (Gardiner 1990).

Nevertheless, the derivation of the expected number of animals counted in a given frame (see below) is general for any movement model that results in a HR pattern.


According to Dubkov and Spagnolo (2007), the Langevin equation is given by: eqn 1 where denotes the particle displacement.

This formulation splits a deterministic force term (i.e., the potential field within which a particle is moving), , from a stochastic stimulus term, , which is Gaussian-distributed (white noise) with zero mean, zero covariance between the two dimensions (i.e., spatial coordinates), and the same variance (ɛ) in each spatial dimension.

Concerning the deterministic force, the simplest choice for the case of a HR pattern is a harmonic, time-invariant, potential field given by: eqn 2 where k denotes the strength of the harmonic force.


We derive the Hutchinson-Waser's postulate according to the following assumptions:


(i) A given camera detects (detection probability = 1) any animal within an area measured with negligible error (detection area).


(ii) Animals move independently from one another.


Computer simulation experiments have been conducted to explore the reliability and sensitivity of the proposed derivation (in terms of accuracy and precision), and its usefulness and limitations (in terms of applicability to realistic scenarios).

Conventional sensibility analysis implies to explore the effects of any combination of the involved variables.

Here, provided the large number of variables potentially involved in affecting the quality of density estimates and the fact that most of them are correlated (see below), instead of exploring the full universe of combinations of the range of possible values for each of the considered variables, only a few number of them representing well-differentiated animal archetypes were selected.

Archetypes were defined aiming to identify the key biological features of a given animal that may affect the quality of the estimates.

Therefore, the pattern depicted in the results section should be interpreted as general guide since the archetypes are only defined by the selected variables and other species-specific characteristics are ignored (see more discussion below).


A comprehensive search was conducted using Google Scholar and Web of Science to compile species of any taxa for which data on four variables that beforehand were presumed to affect the quality of density estimates (density, body mass, speed and HR size) were available.

Different combinations of keywords (HR, biomass, density, abundance, movement, speed and velocity) were used.

The reference list of any reference resulting from this primary search was in turn checked to identify additional data.

Finally, when information for one of the


Invariant settings were preferred to facilitate the archetype comparisons.

Accordingly, the radius of the circular area within which any animal is detected (camera radius) was defined in a way that, on average, m animals per frame are counted: eqn 12 where D is the actual animal density of a given archetype.


A virtual camera was set at the centre of a squared scenario with side defined as: eqn 13 where Radius is the radius of the HR.

The rationale of defining such a buffer (2*Radius) is that an animal with its HR centre outside the scenario considered (and thus not included in the simulation settings) has a negligible probability of being detected by the camera.

The number of animals to be moved within such a scenario is given by side 2 *D.


The HR centres of the simulated animals were randomly distributed within the virtual scenario (arena), and each animal was moved according to eqn 3.

The movement parameters k and ε were estimated (eqns 5 and 6) using the data compiled as described above.

Product ∆t*k was set to 0.1 to ensure negligible error related to the discretization of the movement equation (eqn 3).

Note that this causes the time step, ∆t, to be scale invariant.


Ten cameras were set in each simulation experiment.

The positions of all simulated animals were actualized at each of 300 time steps.

The number of animals within the area detected by the camera was recorded every 5 time steps from the 5 th through the 300 th time step (i.e., up to 60 frames per simulation experiment).

Temporal autocorrelation in the counts of the same camera was tested with the acf function in the R program (http://www.r-project.org/).

Up to 15 independent simulation experiments (i.e., a new set of animals was created and moved in a new scenario) were replicated for each archetype.

For each of these 90 experiments, the obtained dataset was a matrix of 60 rows (i.e., count of animals detected per frame in 60 frames) and 10 columns (cameras).


Animal density was estimated by a Bayesian implementation of eqn 11 using the jags function from the R2jags package (Su & Yajima 2015).

A uniform prior between -30 and 30 was set for µ, which translates into densities between 9.3×10 -14 and 1.1×10 13 .

A gamma-distributed prior with shape = 0.001 and rate = 0.001 were set for tolerance, which is the squared inverse of sd (eqn 11).

For each dataset, five Markov chain Monte Carlo (MCMC) simulations were run.

We drew 12,000 posterior samples, discarded the initial 2,000 iterations (burning period), and one out of 50 of the remaining iterations were kept to prevent autocorrelation (thinning strategy).


The convergence of the MCMC chains was assessed by visual inspection of the chains and was tested using the Gelman-Rubin statistic (Plummer et al. 2006).

A threshold value of 1.1 or less was assumed to suggest convergence (Gelman et al. 2013).


Generally, the usefulness and applicability of any method depends on the effort needed to achieve a target accuracy and precision.

Here, the effort can be expressed as the number of cameras and/or the deployment time.

Accordingly, each of the 90 simulated datasets (i.e., the count of animals detected per frame in 60 frames of 10 cameras) was submitted to 60 analyses (i.e., the i th analysis included the first frame to the i th frame).

Therefore, a total number of 5,400 analyses was completed (6 archetypes, 15 independent simulations and 60 analyses per simulation).


Accuracy refers to how close an estimated parameter is to the true value.

Here, it was defined as the scaled root mean squared error (SRMSE; Walther & Moore, 2005): , eqn 14 where D was the true density, was the median of the Bayesian posterior distribution, and n was the number of replicates (n = 15).


Precision refers to the variability around the parameter estimate.

Here, it was defined by the coefficient of variation (CV), which provides a scaled measure of precision, thus allowing a mean-independent comparison between archetypes (Walther & Moore 2005): eqn 15 where SD refers to the standard deviation, and refers to the mean of the medians of the posterior distributions of the 15 replicated simulation experiments.


Finally, coverage was assessed by the percentage of analyses for which the 95% Bayesian credibility interval (BCI) of the posterior distribution of the density estimate included the true value.


Nearly a thousand references (n = 980) provided data for at least two of the variables that beforehand were presumed to affect the quality of density estimates (density, body mass, speed and HR size), but data for all these variables were available for only 41 species (see Data Accessibility section and references list at Appendix S3).

The correlation patterns between these variables were remarkable (see Fig. S1); further, the first two PCA axes explained 90% of the total variability (Fig. 1) and revealed two independent patterns: PC1 (explaining 64.0% of the variance) was well correlated with density, HR size and biomass, and PC2 (explaining 25.6% of the variance) was well correlated with speed.


Based on these two independent axes, six well-contrasted archetypes were selected by visual inspection.

The features of the archetypes were assigned from a freshwater fish (Campostoma anomalum (Rafinesque, 1820)), a marine fish (Chaetodon baronessa (Cuvier 1829)), a marine mammal (Monodon monoceros (Linnaeus, 1758)), a bird species (Brachyramphus marmoratus (Gmelin, 1789)), a terrestrial mammal (Alces alces (Linnaeus, 1758)) and a terrestrial reptile (Testudo graeca (Linnaeus, 1758)).

Hereafter we refer them as freshwater fish-based (F/F-arch), marine fish-based (M/F-arch), marine mammal-based (M/M-arch), seabird-based (M/B-arch), terrestrial mammal-based (T/M-arch) and terrestrial reptile-based (T/R-arch) archetypes, respectively.


The movement parameters for a BRW (k, ε, and ∆t in eqn 3) of these archetypes were estimated (eqns 5 and 6) from the values of speed and HR size reported in Table 1.

Reliable values of camera radius (in relation to body mass) were obtained, ranging from 0.36 m to 630.8 m with m = 0.5 (eqn 12).

However, in the specific case of the M/F-arch , the archetype with the smallest HR size, we fixed the mean number of counts per camera up to 1.5 to increase the number of animals to be simulated (Table 1).


After completing 5,400 analyses of the data from 90 simulation experiments, more than 90% of the BCIs included the true value irrespective of the sampling effort and archetype, suggesting the proper retrieving of the density (Fig. 2, Table 2).


The general statement that accuracy and precision improve with an increase in sampling effort was supported in five out of the six archetypes (Fig. 2), but their densities were slightly underestimated.

In those five cases, the averaged estimates of animal density did not show any substantial improvement after 1000-1500 frames.

However, provided that the frame rate was archetype-specific, such a threshold implied different deployment times (Table 2).

For example, for M/M-arch, accuracy improved 81% from low (50 frames, 14 hours of deployment time) to moderate sampling effort (1500 frames, 17 days) but only 15% from moderate to high sampling effort (3000 frames, 35 days).

The figures for precision were similar (86% and 16%, respectively, Table 2).


When 10 cameras were deployed, the number of frames needed to reach a threshold of 10% accuracy ranged between 100 and 350 frames (Fig. 3a), which corresponded to deployment times ranging from 5 min to 75 days for each of the cameras, and depending on the archetype (Fig. 3b).

After ranking the archetypes based on increasing deployment times, for F/F-arch, 9.3% accuracy and 10% precision were reached after 5 min 24 sec (250 frames); for M/B-arch, 9.6% accuracy and 9.7% precision were reached after 28.8 min (250 frames); for M/M-arch, 9.0% accuracy and 9.3% precision were reached after 28 hours 17 min (100 frames); for T/R-arch, 6.4% accuracy and 6.6% precision were reached after 54 days 10 hours 42 min (300 frames); for T/M-arch, 8.6% accuracy and 8.4% precision were reached after 75 days 7 hours 48 min (350 frames).

When a high effort level was considered (i.e., 3000 frames or from 1 hour for F/F-arch up to 1.7 years to T/M-arch), the SRMSE was under 6.5% for all species, with the exception of the M/F-arch.


Accuracy and precision improved at different rates depending on the archetype because they crucially depended on how well the stationary distribution was reached at a given temporal scale.

The more time a species took in exploring a relevant fraction of its HR, the more sampling time was needed to reach a target quality for the density estimates.

A greater sampling effort was needed either when animals moved slowly (e.g., T/R-arch) or HR sizes were large in relation to the exploration rate (e.g., M/M-arch and T/M-arch) (Fig. 3b).


The case of the M/F-arch broke this general pattern.

This species never reached a 10% error threshold for accuracy nor improved accuracy and precision after increasing the sampling effort (Fig. 3, Table 2).

Likewise, the BCI of the posterior distribution was skewed in all cases


A generalization of the Hutchinson-Waser's postulate has been proposed here to estimate animal densities using terrestrial or underwater cameras (i.e., counts per frame) in species behaving according to the widely observed spatial behaviour that lead to the establishment of a HR area.

The accuracy and precision reached for the density estimates after an affordable sampling effort provide further insight into the potential and comprehensiveness of the method.

The results of the simulation experiments suggested that it would be sufficient to count animals in a few hundred frames adequately spaced in time to provide density estimates with SRMSEs smaller than 10%.

In contrast, the optimal time the cameras should be deployed (i.e., the optimal rate at which the frames should be counted) is species-dependent.

For ten cameras, less than an hour of sampling (i.e., approximately 250 frames) was necessary for fish and bird-based archetypes, but more than 24 hours (i.e., between 100-350 frames) was needed for archetypes with larger HR areas, for which the time to cover the full HR area may range from a fortnight to more than one year (Table 1).

The best estimates in terms of both accuracy and precision were obtained for animals with high densities, small HRs in relation to the exploration rate and large body mass.

Overall, the results from the Bayesian implementation of the model demonstrate that density can be precisely and accurately estimated after an affordable sampling effort, but generally, the faster the animal covers its HR area, the less sampling time is needed.

Nevertheless, some of the archetype-specific results should be interpreted with caution.

For instance, in the case of the M/B-arch, density was accurately estimated after a very short survey time, which is related with its large speed and relatively small HR (Table 1).

The speed value used in the simulation experiments has a relevant impact in the time needed for exploring a relevant fraction of the HR, thus a better reconstruction of the stationary probability can be obtained with smaller sampling effort for faster animals.

However, speed definition is elusive and its magnitude is neither easily nor precisely estimated.

Therefore, the patterns depicted in Fig 2 and 3 are suggesting a general guidance but species-specificities may modify the predicted effort needed for attaining a Accepted Article This article is protected by copyright.


All rights reserved.


desired accuracy and precision.

Hence, the relationship between the optimal sampling design (i.e., the optimal number of cameras, number of frames per camera and deployment time) and the space occupancy pattern of the animal may be complex.

Therefore, it is strongly recommended to complete a pilot study (i.e., case-specific simulation experiments) including both, species-specificities and case-related constraints (e.g., budget available or technological limitations of the cameras) to assess whether the optimal settings are fulfilling or not the objectives in terms of expected accuracy and precision.

For this purpose, R code in Appendix S1 can be easily adapted.


It should be noted, that a slightly systematic underestimation of the true density was detected in all simulations (Fig. 2).

This bias may actually be an outcome of the simulation features instead of a methodological limitation.

During the simulations, the virtual populations are bounded in the virtual scenario by the effective sampling area (eqn 13), and simulated animals could therefore move from inside the area to outside but not vice versa, leading to the aforementioned bias.


In spite of these uncertainties, the method proposed here has several advantages when comparing with increasingly popular video survey methods based on distilling metrics as N-max (i.e., maximum number of animals in a given frame) as a proxy of abundance (Schobernd et al. 2014).

From the conceptual side, the method proposed here provides an estimate for the absolute density, in contrast to the relative density provided by those alternative methods.

In addition, animals must be only counted in a subsample of frames while for N-max a full video must be analysed, which may represent a relevant difference in the time needed for processing the videos.

Metrics as N-max are justified by the fact that they guaranties that the same animal is not recounted.

Counting the same animal twice or even more times is a problem for non-instantaneous estimation methods developed for video surveys (Ward-Paige et al. 2010; Campbell et al. 2015).

However, recounting does not imply any bias for the method proposed here.


When animals move according to a HR space occupancy pattern, there exists a stationary probability density function of finding a given animal at a given position.

Although we have focused on the particular case of the BRW (Börger et al. 2008), the same rationale may be extended to any other potential field and form of the stochastic term that renders a confined pattern of space use.


Contrasting, mark- recapture methods, which are based on a completely different rationale, incorporate repeated identification of the same individuals (e.g., Efford 2004; Royle & Young 2008).

Spatial explicit capture-recapture models aim to estimate the detection probability of any given animal, and that detectability can be disentangled from demographic processes (e.g. emigration/mortality and immigration/birth) given the history of captures (i.e., detections) of any given animal (Chandler Accepted Article This article is protected by copyright.

All rights reserved.

Royle 2013).

Certainly, our approach focuses in estimating animal density only.

However, demographic rates could still be estimable by nesting the method proposed here into frameworks like those developed by fisheries assessment (Hilborn & Walters 1992).


Another advantage of the method proposed here is that animal density can be estimated in a single visit to the sampled area.

Simulation experiments were performed with a subsample of evenly distributed frames, being a convenience choice to facilitate the evaluation of temporal autocorrelation between frames.

However, it may be any random subsample of the frames, after previously ensuring a safe between-frame period with temporal independence.


Therefore, data from conventional camera trapping (i.e., camera is activated when an animal is present) can be easily adapted to this method.

The benefit of motion-triggered camera surveys is that sampling time can be extended over longer periods of time and the resulting data can be broken down in smaller sampling units for analysis (Burton et al. 2015).

Hence, the number of "0" data will be high but expected and with enough time the stationary probability density function of HR centres will be recovered.


Certainly, other approaches can also obtain data from a single visit to the sampled location.

For example, abundance can be inferred from occupancy models, which are primarily concerned with distribution (i.e., presence/absence), but in those cases individuals must be identified (recounting is a severe concern for the method (Royle 2004; Guillera-Arroita 2017)), and repeat surveys within the single visit are required (Marques et al. 2017).


Another advantage of the proposed method is that, neither stringent assumptions nor precise data on movement features are needed to estimate densities (but to define the optimal sampling settings some rough idea is required, Appendix S1).


When using wildlife video recording methods, specific models that relate animal density with encounter rates have been widely considered: the random encounter model (REM), derived from ideal gas models (Hutchinson & Waser 2007), and a closely related approach based on the Formozov-Malyshev- Pereleshin (FMP) formula (Stephens et al. 2006; Keeping & Pelletier 2014), for which animal speed is assumed to be known (Rowcliffe et al. 2008; Cusack et al. 2015).


A drawback of the REM and FMP is the non-instantaneous nature of encounters, which account for the speed- related bias (Ward-Paige et al. 2010).


Also, based on the encounter rates (i.e., detections are equivalent to encounters), distance sampling methods record distances from the observation point (typically line transects) to any detected animal (Buckland et al. 2001) and claim reasonable accuracy only if animals move at less than half the speed of the observer (Ward- Paige et al. 2010).


Thus, in general, encounter-related methods are highly dependent on the assumptions on how animals move (Rowcliffe et al. 2008; Keeping & Pelletier 2014; Glennie et al. 2015; Cusack et al. 2015).


Different alternatives for circumventing this problem have been


Additional Supporting Information may be found in the online version of this article:


Appendix S1.

Guidelines to apply the model to a case study.


Appendix S2.

Evaluating accuracy and precision in patchy landscapes.


Appendix S3.

Supplementary bibliography. .


Fig. S1.

Bivariate correlations between densities, body mass, speed and HR size.


Researchers have striven for many decades to find better and better methods to estimate the size, or the density, of natural populations, and the development of camera traps (CT) has stimulated the research of new methods for population assessment [1].

In a recent paper in the Journal of Animal Ecology, using CT to assess the size of natural populations, Campos-Candela et al. ( 2018), hereafter CC, claimed that ‘the absolute density is given by the average number of animals counted per frame’ [2].

Ideally, the method proposed by CC is perfect for wildlife managers: easy to use and cheap.

CC developed their approach according to a theoretical framework where animals are assumed to behave as particles of an ‘ideal gas’ [3].

Since such an assumption appears difficult to be respected or even reasonably approached in actual animals, CC correctly verified that such a result remains valid also when the animals behave in more realistic ways, specifically when they exhibit home range (HR) behaviour.

Considering the potential relevance of this work to wildlife conservation and management, we have carefully read the paper and noted several problems in the method used to simulate the home ranges and CT detections.

Estimation methods based on capture–mark–recapture (CMR) have been largely used and present many different ramifications including non-invasive genetics [4] and removal methods [5].

Managers usually do not use CMR methods because animals have to be individually identified.

This approach is, however, used routinely when animals are naturally recognizable, for example tigers or whales [6].

Distance sampling, where detectability is estimated by the distance of the animal from a reference point or transect, has been widely used to assess the population size of marine and terrestrial organisms [7].

Since CT are cheap and easy to use, recently several methods have been proposed to estimate the population size of unmarked individuals such as Random Encounter Model (REM) [8], point transects [9], REST model [10], N-mixture models [11] and SECR models [12].

Available methods assume that the population to be assessed is demographically closed.

In practice, this means to perform a snapshot survey, very short in relation to the demography of the species of interest so that deaths, births, immigration and emigration can be overlooked.

For instance, for a large terrestrial mammal, it is reasonable that a survey can last, at most, 30 days in periods when the species is known to be not dispersing, migrating or reproducing, and mortality is low.

When evaluating the simulation results, it is fundamental to consider the coefficient of variation in the estimates, to understand the capacity of the method to perform trend detection [13]; accordingly, Skalski, Ryding, and Millspaugh (2010) suggested that a coefficient of variation <0.2 (20%) is appropriate for sound management [14].

The main reason for this paper is that we believe that given the fundamental importance of population assessment in research and applications, scientists have to avoid statements which may cause an erroneous use of the statistical methodology and, as a consequence, to determine negative impacts on wildlife conservation and management.

Our criticism to the methodology used by CC in the simulations can be summarized in four points: 1.

The derivation of the species-dependent parameters, at the base of their model is incorrect; 2. The rescaling of the detection radius has no reason and is highly misleading; 3.

The time step used is too large to yield correct results; 4.

For some of the archetypes proposed by CC, their model is inappropriate to the biology of the species.


The equation at the base of the CC model describes the evolution of the position X of a Brownian particle subjected to a noise R in a quadratic potential, for example subjected to a restoring force such as a particle attached to a spring, where k represents the elastic constant and XC is the centre of the HR.

The noise R is Gaussian (white noise) with zero mean, zero covariance between the two dimensions (i.e. spatial coordinates) and the same variance in each spatial dimension.

The HR radius depends on the two parameters of model 1, k and 𝜖, as: radiusHR = C1√𝜖/k, where the constant C1 depends on how the HR radius is defined.

To get sensible simulations for the species of interest (in our case the moose), we need to estimate k and 𝜖 from actual data.

For estimating two parameters, we need two equations.

One is given by the home range radius (which is usually known).

For the second equation, CC used the animal velocity which can be estimated from GPS data.

CC used the following equation: <V> = 𝜖(1 − e−2kΔt)∕kΔt, where <|V|> is the velocity magnitude, and Δt is the time step.

This is the critically wrong passage in CC, since in model 1 it is not possible to define a mean absolute velocity of the particle since the displacement scales as dt and in performing the limit: v = lim dt→0 dx/dt ∝ lim dt→0 √dt/dt = ∞. For the moose, CC used a HR of 82 km2 by McCauley et al. ( 2015) and the mean speed of 0.033 m/s from Vander Vennen et al. ( 2016), which is based on 1 hr fix sampling.

As shown in Equation 3, the mean speed depends on Δt, k and 𝜖, and to solve this equation, CC were obliged to fix arbitrarily the relation Δt = 0.1/k.

Unfortunately, this approach yields a Δt of 10 hr, quite different from the actual time used for fix sampling by Vander Vennen et al. ( 2016).

However, as seen in Equation 3, the movement model (Brownian motion) used by CC implies that the speed is dependent on Δt.

If we compute back the speed at 1-hr intervals using the value found for 10 hr, we find that the animals move at the speed of 0.112 m/s instead of the true velocity of 0.033 m/s, almost four times faster, which is clearly wrong.

In the case of moose, for which we have made the computation, this implies that the simulations of CC reduce very much the CV of the population estimates, simply because a larger number of animals walk through the cross section of the CT field since the animals move too fast.

Note also that at least three of the other archetypes (Campostoma anomalum, Testudo graeca, Brachyramphus marmoratus) are subjected to a similar error, while Chaetodon baronessa cannot be evaluated due to lack of data.


According to CC, the ‘Invariant settings were preferred to facilitate the archetype comparisons.

Accordingly, the radius of the circular area within which any animal is detected (camera radius) was defined in a way that, on average, m animals per frame are counted’.

This approach makes any comparison with actual CT experiments impossible since only this length scale is rescaled and not all the other parameters, such as the distance between cameras or the HR size.

For a detailed discussion of the topic, see Section S3 in Supporting Information.

In particular in the case of the moose, the camera detection radius was set to 630 m by CC; therefore, the huge HR radius of the moose is almost nine times the camera detection radius which is completely absurd.

Told in another way, such a detection area needs an equivalent of 4,900 ‘true’ CT with a detection radius of 9 m to be sampled.

CC is not mentioning explicitly the type of camera used (motion-triggered or time-lapse); however, from the discussion (p. 833), it appears that CC's method can be applied also to motion-triggered cameras, which are the most frequently used CT [15].

For motion-triggered cameras, the value of Δt ∼ 10 hr used by CC is probably too high to avoid round-off errors in the detection of the animals as sketched in Figure 1.

Since in 10 hr, the average displacement is about 1.26 km, an animal can very easily cross the detection area without being recorded in the simulation, as shown in Figure 1a.

Another source of error is represented by the tortuosity of the Brownian motion between two fixes as shown in Figure 1b.

Indeed, it is possible that an animal whose fixes are outside the detection area may have crossed the detection area during the 10-hr interval.

These errors can considerably reduce the efficiency of the CT-simulated survey, and one needs a very long survey duration to get reasonably high precision even with 10 cameras with 630 m detection radius as done by CC.

We note also that this part of the description of the method of CC is quite unclear.

This criticism is not appliable in case of the use of time-lapse CT.

Usually, wildlife managers use motion-triggered cameras because this method is more informative than time-lapse sampling.

However, there are monitoring methods that require time-lapse methods [16].


Finally, for one of the archetypes used by CC, Diomedea calonecrtis, the motion of birds at large scales is not Brownian-like diffusive as supposed by CC model, but on the contrary Lévy-like super-diffusive [17].

We propose a model where the equation of the velocity is the sum of three terms.

The first one tends to bring the velocity of the animal close to the characteristic speed of the species Va, the second one is an acceleration towards the centre of the HR and the third component is a random noise.

The velocity yields the displacement X of the animals: V(t + Δt) = V(t) Va + (V(t) − Va)e−Δt∕𝜏 V(t) − K(X − Xc)Δt + R, X(t + Δt) = X(t) + V(t)Δt, where V(t) is the velocity magnitude of the animal at time t and τ is the time-scale of the fluctuation on the magnitude of the velocity.

In our model, the velocity, not the displacement, tends to be oriented towards the centre; note that K has dimension 1/t2 while k (Equation 1) has dimension 1/t.

An instance of a simulated trajectory is shown in Figure S3.

According to a large body of literature, for short times the direction of movement, that is the angular component of V(t) has a persistence (correlated random walk, Turchin, 1998), while for long times the trajectory resembles the one of the model 1.

While CC's model assumed a complete independence of movement direction from step to step, more realistically, we assume that, in the short term, directions are correlated, that is animals perform a correlated random walk.

More detailed explanations are reported in Section S1.

We define an arena of 10 × 10 km with periodic boundary conditions.

Inside this arena, we set a squared grid of equidistant cameras, from a minimum of 16 to a maximum of 100 samplers (i.e. 4 × 4 to 10 × 10), as commonly done in these kinds of studies.

Here, we report only the scenario with 8 × 8 cameras but in the Section S2.2, we report also the other cases.

We simulated three different animal densities: low, 0.1 animals/km2, normal, 0.4/km2 (the same value used by CC), and high, 1/km2.

The coordinates of the HR range centre are randomly assigned.

Animals move according to Equation 5 and are recorded by cameras when the camera–animal distance is lower than the detection radius (we used a ‘usual’ detection radius, 5 m, and an ‘optimistic’ radius of 9 m).

We performed two sets of simulations.

In the first scenario, simulated moose maintain a constant speed as assumed by CC.

However, to assume that the speed is constant during the day is clearly wrong in moose (and in any other animal) as shown, for instance, by Van Ballenberghe and Miquelle (1990) where active displacements take a short part of the daytime while the remaining time is allocated to resting/rumination and grazing.

Thus, in the second scenario, we simulated a moose population with two possible behavioural modes: active and resting (which also include grazing).

According to Van Ballenberghe and Miquelle (1990) movements take about 7% of the activity budget.

We also assumed that in resting mode there is no movement.

In a third scenario, we assume a more realistic 3-mode activity patterns where we differentiate among no movement, grazing and moving, respectively, 62.7%, 30.4% and 6.9% of the activity budget.

Since this set of simulations have yielded very similar results to the one of scenario 2, the results are presented in Section S2.3.

To be consistent, the velocity of the moose in scenarios 2 and 3 is calculated in order to have the same mean overall velocity as in scenario 1, calculated as a weighted mean.


The statistical estimator proposed by CC yields asymptotically unbiased estimates of population size (Figure 2).

In case of constant animal speed and large detection radius of CT (Figure 2a), the estimate attains the prescribed CV threshold in less than 30 days at least for large and intermediate populations, while, unsurprisingly, for the lowest density value, the precision is too low to be acceptable.

On the contrary, if we simulate animals characterized by two different activity patterns, we observe a rapid decay of the precision of the statistical estimator (Figure 2b).

Even for the highest density populations, the result remains quite unsatisfactory.

Since we know a priori that there are important differences in speed within each individual animal, we may conclude, with some degree of generality, that the method proposed by CC cannot represent a practical method for estimating the population size of moose.

As one could expect, when the detection radius is lowered to a more realistic value (5 m), the system generally fails to provide acceptable estimates.

We have also performed one numerical experiment with more realistic activity patterns including resting/ruminating, foraging and moving, but the results remain qualitatively the same (Section S2.3).

Of course, we should not exclude that there can be situations characterized by a set of parameter values (density, HR radius, etc.) where the estimator proposed by CC can work appropriately, but wildlife managers should test, by simulation, if the situation of interest can be precisely surveyed by this method.

We showed that under ideal condition (cf.

Figure 2a) the estimator is able to correctly evaluate the population size under reasonable study conditions (high/medium density, large camera detection radius).

However, the introduction of more realistic constraints (e.g. two or more different activity modes) led to a strong deterioration in the performance of the estimator.

In other words, the method is scarcely robust to variations in parameter values.

We have to stress that under natural conditions, where there is an intrinsic and uncontrolled variability, one needs statistical methods robust to limited violations of the assumptions and characterized by a reduced propagation of uncertainty.

If a statistical estimator is very sensitive to the details of the movement patterns, or to random fluctuations in parameter values, the system becomes practically useless, or it may request a complicated modelling study which is usually outside the skills of wildlife managers.

Hayward and Laupacis (1993) made it clear that statistical robustness is fundamental to develop appropriate wildlife monitoring programmes [18].

Note that we have assumed that our samplers detect all animal in areas of 78.5 and 254.5 m2.

In the second case, the resulting cross section of our monitoring design is quite optimistic since, in the field, the area where a CT has a certain detection probability is no larger than 4 m2 (with a dependence on several parameters such as body mass, movement speed, etc., Nakashima et al., 2018) [10]; further, the shape of the camera field of view (FOV) is not circular but roughly triangular.

If we should have used more realistic values for the FOV, we would have obtained worse CV values than the ones we reported in Figure 2; however, we used very conservative values because we wished to show that discouraging results were independent of the camera detection area.

A basic problem of naive methods used to estimate the population size via camera trapping is that one has to assume a certain probability of detection, an assumption which, to be respected, reduces a lot the area covered.

Howe et al. ( 2017) showed experimentally that in CT the detection probability gets <1 at distance around 6–7 m (for Philantomba maxwelli, a small antelope) and wildlife managers should take very seriously this limitation of CT [9].

The simulation model of CC was affected by errors which could improve but also deteriorate the efficiency of the proposed estimator.

Such concerns obliged us to develop a simple but more consistent model to describe the behaviour of the animals in order to correctly evaluate the efficiency of the estimator proposed by CC.

To evaluate monitoring methods, it is important to keep in mind what are the practical constraints encountered in the field, which is not the case when CC used, for moose, a detection radius of 630.8 m, which yields a covered area of 1.28 km2, a surface which needs almost 5,000 CT to be sampled.

The problem here it is that CT can be used in practice whether their number is limited because a huge amount of manpower is necessary to review the videos/pictures and to install/remove the CT from the field.

In agreement with CC, in Section S2.2 we showed that good results can be obtained using hundreds or thousands of cameras but such numbers are outside any practical possibility of use.

The technical evolution of more and more efficient camera traps has stimulated the development of new methods of population assessment which is of the greatest interests for ecological research, conservation and management.

The different methods proposed in literature are all correct in mathematical–statistical sense, when their assumptions are respected.

However, this analysis of CC methods showed that this condition it is necessary but not sufficient given the limitation in the sampling effort and the sensibility to the violation of the assumptions, violations which for sure are present during a field survey.

Now, we miss a comparative analysis of the different proposed methods in order to indicate to wildlife managers and practitioners the best method and its precision that can be used in different field conditions.

With this paper, we hope to stimulate deeper insights on the matter.


Evaluating absolute population density is an extremely complex task that requires strengthening the links between theorists and empiricists.

Both, Campos‐Candela, Palmer, Balle, and Alós (2018) and Abolaffio, Forcadi, and Santini (2019), contributed to this challenge from the theoretical side; the first one by demonstrating a theoretical postulate to estimate absolute densities from camera counts; the second one by exploring the proposed method for a specific species (the moose, Alces alces) [1].

Note, however, that the undifferentiated use of model, method and simulation terms in Abolaffio et al. ( 2019), when addressing concerns exclusively about our simulation procedure or the applicability of the method for a particular case, may be misleading.

Concerning the camera-based method, our key contribution is that, for the case of animals whose movement leads to a stationary spatial pattern, absolute animal density can be properly estimated from the average number of animals counted per frame whenever a number of assumptions are met [2].

The underlying model to this method states that, for a given camera, the number of animals’ counts per frame is given by a Poisson distribution with mean equals to the product of the true animal density, the detection area of the camera and the probability of detection [3].

Essentially, our model is equivalent to determine the distribution of the space occupation in time, which is a question that has been largely discussed from the probabilistic perspective [4].


In response to criticism (1), features for the implemented simulations were dictated by mathematical convenience in order to avoid extremely large computing times.

In sake of simplicity and generality, we decided to use the simplest version of a biased random walk model (BRW; Codling, Plank, Benhamou, & Interface, 2008) as a mathematical approximation for movement to make inference about density estimates [5].

BRW results from combining an elastic drift (k) that pulls the animal towards the HR centre, and a stochastic component [6].

The resulting space use will be characterized by a stationary probability density function with independence on the nature of the stochastic term [7], and that will emerge when the stochastic part is either Gaussian or, for example, a Lévy-like diffusive term [8].

In the BRW model used, when the drift force equals 0, the movement reduces to a random walk diffusion model [9].

Equalling the stochastic term to 0, as Abolaffio et al. ( 2019) discussed, will lead to a linear trajectory towards the HR centre, where the animal will remain forever, which is not biologically meaningful.

In any case, a BRW with a Gaussian stochastic component is the simplest choice for simulating animal trajectories but any other movement model meeting the requirement of stationary criteria should be considered when addressing the particularities of a given species.


In response to criticism (2), fixing the mean number of counts per camera was a criterion for getting some invariance and thus for facilitating the comparison between archetypes.

In this way, any potential effect of density itself is not confounded with the effects of HR size and/or exploration rate.

In our simulations, the continuous movement trajectory was approximated as a series of discrete time steps, Δt, that may affect some properties of the movement pattern [10].

In agreement with the criticism (3) in Abolaffio et al. ( 2019), as a consequence of the discretization for the BRW model in Campos‐Candela et al. ( 2018), the estimated speed depends on Δt.

In general, speed spread increases and tends to be underestimated when Δt increases [11].

Then, when simulating specific-species animal movement, setting a small Δt is advisable.

However, given that animal movement is an inherently autocorrelated process in space and time [12], counting animals at each tiny Δt may result in statistically dependent samples.

Typically, temporal autocorrelation diminishes as observations are made farther apart in time; but autocorrelation in movement data often persist over long-time periods [13].

The optimal solution for the simulation settings would be to move the animals with a tiny Δt but to count the animals at a longer time period.

The compromise solution we adopted was to set the product k * Δt small enough (i.e., 0.1), which still ensured a reasonable discretization of the movement path while speeding up the iterative process in simulations.

Besides, and more important, this commitment decision was not affecting the main purpose of simulations: to obtain snapshots of the system while minimizing autocorrelation.


As stated above, the estimated sampling effort inferred from our simulations is only an approximation.

When dealing for specific-species cases, many variables may modulate the actual effort needed for achieving a desired precision for density estimates.

For example, the larger the area surveyed by the camera is, the smaller the number of frames/cameras needed for achieving a target precision will be.

However, the pixels density imposes an obvious limit, which in addition will be species-dependent because, for a given pixel density, a larger area could be covered by larger-sized animals.

Similarly, the larger the number of cameras is, the better the precision will be.

However, the total number of cameras needed for a target precision can be out of the available budget for certain cases.

For two of the explored archetypes, the terrestrial mammal-based and the terrestrial reptile-based archetypes, the optimal sampling settings to recover stationary density of the HR centres with a target level of precision implied large sampling times along with big camera areas.

Particularly, for the case of the terrestrial mammal-based archetype, when using 10 cameras with an area of detection of 630 m, the estimated sampling effort was of 11 days for a target level of precision of 0.2 (i.e., five frames analysed by camera); and 645 days for a target level of precision of 0.05 (i.e., 300 frames analysed by camera).

In both cases, frames were 2 days apart one from other to avoid autocorrelation.


Interestingly, results from the terrestrial mammal-based archetype are not so far when evaluating the case of moose with a more detailed movement model by Abolaffio et al. ( 2019).

Abolaffio et al. ( 2019) explored our method from different perspectives and simulated scenarios as realistic as possible for a particular species case.

Camera trapping (CT) radius was set to 5 or 9 m and variable movement speed (with two behavioural states) was considered.

From the results shown, to reach a target level of precision of 0.2 may require around 1,250 or 2,500 cameras, respectively, sampling during 30 days (no information on the number of frames sampled by camera nor the time between frames to control for autocorrelation is provided).

Therefore, both simulation strategies agreed in that the target precision level can be reached within 30 days either by increasing the camera radius (i.e., low number of cameras with wide range of detection; Campos‐Candela et al., 2018) or by increasing the number of cameras (i.e., with shorter detection radius; Abolaffio et al., 2019).

These observations actually demonstrate that the underlying dynamic system is ergodic.

In any case, the results from Abolaffio et al. ( 2019) corroborate the usefulness of our model, as they outlined in different parts of the text: ‘The statistical estimator proposed by CC yields asymptotically unbiased estimates of population size […].

In case of constant animal speed and large detection radius of CT […], the estimate attains the prescribed CV threshold in less than 30 days at least for large and intermediate populations, while, […], for the lowest density value, the precision is too low to be acceptable’.


Certainly, some combination of sampling settings (either bigger area or a larger number of cameras) may be unreasonable, especially when camera trapping has limited distance of detection [14].

In this line, Abolaffio et al. ( 2019) pointed out that ‘[…] such a detection area needs an equivalent of 4,900 “true” CT with a detection radius of 9 m to be sampled’, something ‘completely absurd’.

However…why should it be considered ‘absurd’?

We agree that at a first glance, and with the settings stated by Abolaffio et al. ( 2019), this sampling effort is discouraging but to consider it as a ‘completely absurd’ solution overlooks the real opportunities existing nowadays to make it more reliable than impossible.

We believe that this statement may be short-sighted and unambitious.

In the last years, animal ecology is experiencing a revolution in imaging, camera technology and related technologies (e.g., remote control), which can provide automatically images covering big areas with enough resolution to identify the target species for long-term periods.

For example, images taken from the air will benefit from the use of drones (UAS; Lejeune et al. 2013; Hodgson, Kelly, & Peel, 2013; Linchant, Lisein, Semeki, Lejeune, & Vermeulen, 2015; or UAVs; Groom et al., 2013), or particular vertical take‐off and landing aircraft versions (VTOL; Goebel et al., 2015); whose relatively low cost is an additional attribute that makes these devices appealing for wildlife census applications [15].

Besides, the use of gigapixel snapshots discussed in Brady et al. ( 2012) and very high spatial resolution satellite image-data for wildlife counts offer novel panoramic windows for sampling very large areas [16].


Abolaffio et al. ( 2019) pointed out that they would need an equivalent of 4,900 cameras to estimate abundance in their species case study.

Around 300,000 participants (cameras) have submitted around 300 million bird pictures to the citizen science programme ‘eBird’ since 2002.

Obviously, it is not comparable for the case of the moose; however, it offers an idea of the potential working frame for methods like the one developed in Campos‐Candela et al. ( 2018).

Moreover, to efficiently exploit the increasing resources from digital imagery, there is a need for an urgent shift from manually counting animals by human experts, which is certainly expensive, to automatic methods, where machine learning offers a big window of opportunities for extracting information [20].

These opportunities altogether will provide a huge amount of data in the next future that will require proper statistical approaches to estimate abundance.

In such a context, the main contribution in Campos‐Candela et al. ( 2018): for the case of animals whose movement leads to a stationary spatial pattern, absolute animal density can be properly estimated by the average number counts per frame whenever assumptions for the model meet; can provide the basis for the further assessment of wildlife by using camera sampling.

We must continue to strive to accommodate our proposed model to the particularities of the study system and overcome its potential drawbacks.

However, we really feel that the debate should not only focus on the applicability of the proposed method in Campos‐Candela et al. ( 2018) for some species and case studies; but on the opportunities that it offers in the nearest future for wildlife assessment to many scientists and managers.

Overall, this task requires strengthening the links between theorists, empiricists and engineers, but perhaps it would provide one of the most exciting fields for modern ecology in light of the increasing and unprecedented amount of ecological data.


The aerodigestive tract facilitates the combined functions of breathing, vocalising, and swallowing.

Any dysfunction in this system may lead to oropharyngeal dysphagia (OD) J. Clin.

Med. 2022, 11, 776. https://doi.org/10.3390/jcm11030776 https://www.mdpi.com/journal/jcm or swallowing problems [1].


OD can be the result of underlying diseases such as stroke or a progressive neurological disease (e.g., Parkinson's disease, multiple sclerosis) or an adverse effect after head and neck oncological interventions (e.g., radiation or surgery) or intensive care treatment (e.g., intubation and tracheostomy).


Prevalence estimates of OD have been reported to be as high as 50% in cerebral palsy [2], 80% in stroke and Parkinson's disease, and over 90% in people with community-acquired pneumonia [3].


OD can have a severe impact on a person's health as it may lead to dehydration, malnutrition, and even death.

Research has identified inverse bidirectional relationships between decreased health-related quality of life and increased OD severity [4].


Traditional OD therapy may include physical interventions such as: bolus modification and management (e.g., adjusting the viscosity, volume, temperature and/or acidity of food and drinks); oromotor exercises; body and head postural adjustments; and swallow manoeuvres (e.g., manoeuvres to improve food propulsion into the pharynx and airway protection) [1].

Therapy may also include sensory stimulation, which involves applying techniques like thermal stimulation and chemical stimulation using natural agonists of polymodal sensory receptors (e.g., capsaicin, the spicy component of peppers) [5].


Another type of stimulation considered to be beneficial for promoting rehabilitation of swallowing dysfunction is acupuncture.

This practice emerged from traditional Chinese medicine and exerts therapeutic effects by inserting thin needles at strategic places, termed acupuncture points, on the body surface aiming to rebalance the flow of energy or life force ('qi').

Needles are then activated through specific manual movements or electrical stimulation.

Although stimulation of acupuncture points seems to be associated with places where nerves, muscles, and connective tissues may be stimulated [6], their intrinsic mechanisms are still part of a continuing scientific debate on acupuncture.


Recently, an increasing number of studies have been published on alternative in- terventions aiming to enhance neural plasticity by using non-invasive brain stimulation (NIBS) techniques.

Repetitive transcranial magnetic stimulation (rTMS) and transcranial direct current stimulation (tDCS) are cortically or centrally applied NIBS techniques.

Using electromagnetic induction, rTMS results in depolarisation of post-synaptic connections, whereas tDCS uses direct electrical current to shift the polarity of nerve cells [7].

Alterna- tively, electrical stimulation techniques like pharyngeal electrical stimulation (PES) and neuromuscular electrical stimulation (NMES) target the peripheral neural pathways [8].

NMES aims to strengthen muscular contractions during swallowing and uses stimula- tion by electrodes placed on the skin over the anterior neck muscles to activate sensory pathways [9-11].

In contrast, PES has been shown to drive neuroplasticity in the pharyn- geal motor cortex through direct stimulation of the pharyngeal mucosa via intraluminal catheters [7].


Over the past decade, several reviews have been published on the effects of neu- rostimulation in patients with OD.

Most of these reviews focused on selected types of neurostimulation: NMES [10,12], rTMS [13,14], tDCS [15], or rTMS and tDCS [16,17].

Only two systematic reviews included both cortical (rTMS and tDCS) and peripheral neu- rostimulation (PES and NMES) [18,19].

All reviews targeted interventions in post-stroke populations except one review that broadened inclusion criteria to patients with acquired brain injury including stroke [16].

To date, all systematic reviews on neurostimulation as a treatment for OD set boundaries for inclusion based on medical diagnoses.


The aim of this systematic review is to determine the effects of neurostimulation in people with OD without excluding populations based on medical diagnoses.

Findings are based on the highest level of evidence only, namely randomised controlled trials (RCTs), and summarised by conducting meta-analyses.

The results of this review will be presented in two companion papers.

This paper (Part I) reports on pharyngeal and neuromuscular electrical stimulation (PES and NMES) while the second paper (Part II) will report on brain stimulation (i.e., rTMS and tDCS).


The methodology and reporting of this systematic review were based on the Preferred Reporting Items for Systematic Reviews and Meta-Analyses (PRISMA) 2020 statement and checklist (Supplementary Tables S1 and S2) which aim to enhance the essential and transparent reporting of systematic reviews [20,21].

The protocol for this review was registered at PROSPERO, the international prospective register of systematic reviews (registration number: CRD42020179842).


Literature searches to identify studies were conducted on 6 March 2021, across four databases: CINAHL, Embase, PsycINFO, and PubMed.

Publication dates of coverage ranged from 1937-2021, 1902-2021, 1887-2021, and 1809-2021, respectively.

Additional searches, including checking the reference lists of eligible articles, were performed.

Two main categories of terms were used in combination: (1) dysphagia and (2) randomised control trials.

Search strategies were performed in all four electronic databases using sub- headings (e.g., MeSH and Thesaurus terms) and free text terms.

The full electronic search strategies for each database are reported in Table 1.

To identify other literature beyond that found using these strategies, the reference lists of each eligible article were checked.


Studies were included in this systematic review if they met the following criteria: (1) participants had a diagnosis of oropharyngeal dysphagia; (2) the study included non- invasive neurostimulation interventions aimed at reducing swallowing or feeding problems; (3) the study included a control group or comparison intervention group; (4) participants were randomly assigned to one of the study arms or groups; and (5) the study was published in the English language.


Interventions such as non-electrical peripheral stimulation (e.g., air-puff or gustatory stimulation), pharmacological interventions and acupuncture, were considered out of the scope of this review, and thus were excluded.

Invasive techniques and/or those that did not specifically target OD (i.e., deep-brain stimulation studies after neurosurgical implementation of a neurostimulator) were also excluded.

Conference abstracts, doctoral theses, editorials, and reviews were excluded.


Finally, only studies reporting on peripheral neurostimulation (i.e., PES and NMES) were included in this review (Part I).

Studies on brain neurostimulation (i.e., rTMS and tDCS) will be reported on in a companion paper (Part II).


The methodological quality of the included studies was assessed using the Revised Cochrane risk-of-bias tool for randomised trials (RoB 2) [22].

The RoB 2 tool identifies five domains to consider when assessing where bias may have been introduced into a randomised trial: (1) bias arising from the randomisation process; (2) bias due to deviations from intended interventions; (3) bias due to missing outcome data; (4) bias in measurement of the outcome; and (5) bias in selection of the reported result.

The RoB 2 gives a series of signalling questions for each domain whose answers give a judgement (i.e., "low risk of bias," "some concerns," or "high risk of bias"), which can be evaluated to determine a study's overall risk of bias [22].


A data extraction form was created to extract data from the included studies under the following categories: participant diagnosis, inclusion and exclusion criteria, sample size, age, gender, intervention goal, intervention agent/delivery/dosage, outcome measures, and treatment outcome.


Titles and abstracts of included studies were screened for eligibility by two indepen- dent reviewers, after which the eligibility of selected original articles was assessed by these same two reviewers.

If agreement could not be reached between the first two reviewers, a third reviewer was consulted to reach consensus.

Two independent researchers also assessed the methodological study quality and, where necessary, consensus was reached with involvement of a third reviewer.

As none of the reviewers have formal or informal af- filiations with any of the authors of the included studies, no evident bias in article selection or methodological study quality rating was present.


Data points across all studies were extracted using comprehensive data extraction forms.

Risk of bias per individual study was assessed using the RoB 2 tool [22].

Data were extrapolated and synthesized using the following categories: participant characteristics, inclusion criteria, intervention conditions, outcome measures and intervention outcomes.

Effect sizes and significance of findings were the main summary measures for assessing treatment outcome.


Data were extracted from each study to compare the effect sizes for the following: (1) pre-post outcome measures of OD and (2) mean difference between neu- rostimulation and comparison controls in outcome measures from pre- to post-intervention.

Control groups may receive no treatment, sham stimulation and/or traditional dyspha- gia therapy (DT; e.g., bolus modification, oromotor exercises, body and head postural adjustments, and swallow manoeuvres).

Only studies using instrumental assessment (e.g., videofluoroscopic swallow study (VFSS) or fiberoptic endoscopic evaluation of swal- lowing (FEES)) to confirm OD were included.


Data collected using outcome measures based on visuoperceptual evaluation of instru- mental assessment were preferred over clinical non-instrumental assessments.

Oral intake measures were only included if no other clinical data were available, whereas screening tools and patient self-report measures were excluded from meta-analyses altogether.

When selecting outcome measures for meta-analyses, reducing heterogeneity between studies was a priority.

Consequently, measures other than the authors' primary outcomes may have been preferred if these measures contributed to greater homogeneity.


To compare effect sizes, group means, standard deviations, and sample sizes for pre- and post-measurements, data were entered into Comprehensive Meta-Analysis Ver- sion 3.3.070 [23].

If only non-parametric data were available (i.e., medians, interquartile ranges), data were converted into parametric data for meta-analytic purposes.

Studies with multiple intervention groups were analysed separately for each experimental-control comparison.

If studies included the same participants, only one study was included in the meta-analysis.

For studies providing insufficient data for meta-analysis, authors were contacted by e-mail to request additional data.


Effect sizes were calculated in Comprehensive Meta-Analysis using a random-effects model since it was unlikely that studies would have similar true effects due to variations in sampling, participant characteristics, intervention approaches, and outcome measurements.

Heterogeneity was estimated using the Q statistic to determine the spread of effect sizes about the mean and I 2 was used to estimate the ratio of true variance to total variance.

I 2 -values of less than 50%, 50% to 74%, and higher than 75% denote low, moderate, and high heterogeneity, respectively [24].

Effect sizes were generated using the Hedges' g formula for standardized mean difference with a confidence interval of 95%.

Effects sizes were interpreted using Cohen's d convention as follows: g ≤ 0.2 as no or negligible effect; 0.2 < g ≤ 0.5 as small effect; 0.5 < g ≤ 0.8 as moderate effect; and g > 0.8 as large effect [25].


Forest plots of effect sizes for OD outcome scores were generated for PES and NMES separately: (1) pre-post neurostimulation and (2) neurostimulation interventions versus comparison groups.

Subgroup analyses were used to explore effect sizes as a function of various moderators depending on neurostimulation type.

For example, outcome measures, medical diagnoses, total treatment duration, total neurostimulation time, and stimulation characteristics (e.g., pulse duration, pulse rate, electrode configuration).

To account for the possibility of spontaneous recovery during the intervention period, only between-subgroup meta-analyses were conducted using post-intervention data.


Comprehensive Data Analysis software was utilized to evaluate publication bias.

The Begg and Muzumdar's test [26] was used to calculate the rank correlation between the standardised effect size and the ranks of their variances.

The Begg and Muzumdar test calculates both a tau and a two tailed p value, with values of close to zero indicating no correlation, while results closer to 1 suggest a correlation.

Where asymmetry is the result of publication bias, high standard error values would correspond with larger effect sizes.

Where larger effects correspond to low values, tau would be positive (with the inverse also being true).

Conversely, when larger effects correspond to high values, tau would be negative.


Publication bias was also evaluated utilising a fail-safe N test.

This measure addresses the question of how many omitted studies would be necessary to nullify the effect.

It refers to the number of studies where the effect size was zero being included in the meta-analysis prior to the result becoming statistically insignificant [27].

When this value is comparably low, there may be reason to treat the results with caution.

When the value is comparably high, however, it can be reasonably concluded that the treatment effect is not nil, although it may be increased due to the omission of some studies.


A total of 8059 studies were identified through subject heading and free text searches from the four databases: CINAHL (n = 239), Embase (n = 4550), PsycINFO (n = 231), and PubMed (n = 3039).

Removing duplicate titles and abstracts (n = 1113) left a total of 6946 records.

A total of 261 original articles were assessed at a full-text level, with articles grouped based on type of intervention.

Four additional studies were found through reference checking of the included articles.

At this stage, no studies were excluded based on type of intervention (e.g., behavioural intervention, neurostimulation).

Of the reviewed 261 articles, 58 studies on neurostimulation were identified that satisfied the inclusion criteria.

As this systematic review reports on PES and NMES interventions only, a final number of 42 studies reporting on peripheral neurostimulation were included in this review.

Figure 1 presents the flow diagram of the reviewing process according to PRISMA.


All included studies are described in detail within Tables 2 and 3.

Specifically, Table 2 presents data on study characteristics including methodological study quality, inclusion and exclusion criteria, and details on participant groups.

The following information is provided for all study groups (control and intervention groups): medical diagnosis, sample size, age and gender.

Table 3 reports on intervention goals of included studies, intervention components, outcome measures, intervention outcomes, as well as main conclusions.


Across the 42 included studies, 30 studies reported on NMES and eight studies reported on PES.

Four studies used another type of neurostimulation (i.e., rTMS) in addition to NMES or PES, either within the same group or different treatment groups.


Participants (Table 2).

The 42 studies included a total of 2281 participants (mean 54.3; SD 39.1).

The sample sizes ranged from the smallest sample of 16 participants [60,61] to the largest sample of 162 participants [36].

By intervention type, samples were characterized as follows: NMES total 1706, mean 56.9, SD 38.9, range 18-135; PES total 410, mean 51.3, SD 49.0, range 16-162; and combined neurostimulation total 165, mean 41.3, SD 19.3, range 18-64.

The mean age of participants across all studies was 61.8 years (SD 15.3), with one study reporting age range only (65-93 years) [61].

Participant mean age across all studies ranged from 4.2 years [54] to 84.4 years [39].

The mean age of participants by intervention group was: NMES 60.9 years (SD 16.9), PES 64.7 years (SD 11.9), and combined neurostimulation 63.8 years (SD 6.4).


Across all studies, 61.0% (SD 13.5) of participants were male and one study did not report gender distribution [30].

Percentage of males by intervention group was NMES 62.6% (SD 14.0), PES 56.7% (SD 9.6), and other/combined 65.4% (SD 12.3).

Most studies included stroke patients (n = 31), while three studies included mixed populations [28,41,43] and one study reported OD without further underlying medical diagnosis [39].

Other diagnoses by intervention group were: Parkinson's disorder (n = 2) [32,46], cerebral palsy (n = 2) [50,54], and head and neck cancer (n = 2) [36,48] in NMES; and multiple sclerosis (n = 1) [63] in PES.


Across the 42 studies, VFSS was most frequently used to confirm participant's diag- nosis of OD (n = 31), whereas six studies used FEES [49,53,54,60,64,65].

Several of these studies combined instrumental assessment with either a screen (n = 2) [58,65] or clinical assessment (n = 6) [49,50,53-55,68].

One study used either clinical assessment or VFSS [50].

One study used a single screen [56], three studies used clinical assessment only [35,38,59], and one study used both [33].

The studies were conducted across 14 countries, with studies most frequently conducted in Korea (n = 11), China (n = 7), the UK (n = 7), Spain (n = 4), Italy (n = 2), Turkey (n = 2), and Germany (n = 2).


Outcome Measures (Table 2).

Outcomes measures varied greatly across all studies included in the review, covering several domains within the area of OD.

The Penetration Aspiration Score was the most reported outcome measure (PAS; 18 studies), followed by Functional Oral Intake Scale (FOIS; 12 studies), Functional Dysphagia Scale (FDS; 5 studies), Dysphagia Severity Rating Scale (DSRS; 5 studies), Swallowing Quality of Life questionnaire (SWAL-QOL; 4 studies), and Dysphagia Outcome and Severity Scale (DOSS; 3 studies).


NMES Intervention (n = 30: Tables 2 and 3).

In total, 22 studies included two study arms or groups, whereas eight studies included three groups [31-34Control groups included mostly sham NMES stimulation and/or DT.

Only one study included a control group receiving neither DT nor NMES [30], and one study included usual care across different healthcare settings as the comparison group [51].


PES Intervention (n = 8: Tables 2 and 3).

All eight studies compared PES to a sham version of the treatment [58-65].

None of the studies included other treatment groups (e.g., DT) or control groups (e.g., usual care or no treatment).


Combined Neurostimulation Interventions (n = 4: Tables 2 and 3).

Three studies in the combined intervention group compared three different treatments.

Of these, one study compared PES, paired associative stimulation (PAS) and rTMS [68], a second study compared DT, rTMS combined with DT, and NMES combined with DT [67], and a third study compared rTMS, PES and capsaicin stimulation [66].

A fourth study combined NMES stimulation with sham rTMS or rTMS stimulating different hemispheres (ipsilesional, contralesional or bilateral) [69].


The tau values from the Begg and Mazumdar rank correlation were 0.101 (two-tailed p = 0.589) and < 0.000 (two-tailed p > 0.999) for NMES and PES, respectively.

The NMES meta-analysis incorporates data from 16 studies, which yielded a z-value of 4.107 (two-tailed p < 0.001).

The fail-safe N is 55 indicating 55 'null' studies need to be located and included for the combined two-tailed p-value to exceed 0.050.

Therefore, there would need to be 3.4 missing studies for every observed study for the effect to be nullified.

The PES meta- analysis incorporates data from five studies yielding a z-value of 1.156 (two-tailed p < 0.248).

Since the combined result is not statistically significant, the fail-safe N (which addresses the concern that the observed significance may be spurious) is not relevant.

Both of these procedures (i.e., Begg and Mazumdar rank correlation and fail-safe N) indicate the absence of publication bias.


Figures 2 and 3 present, respectively, the risk of bias summary per domain for all included studies combined and for individual studies.

The majority of studies had low risk of bias with very few exceptions.


Eleven studies were included in the NMES meta-analysis [28sensory NMES stimulation.


Overall within-group analysis (Figure 4).

A significant, large pre-post intervention effect size was calculated using a random-effects model (z(17) = 6.477, p < 0.001, Hedges' g = 1.272, and 95% CI = 0.887-1.657).

Pre-post intervention effect sizes ranged from 0.000 to 3.826.

In 13 of the 18 NMES intervention groups, effect sizes were large (Hedges' g > 0.8), indicating that NMES accounted for a significant proportion of standardized mean difference for these studies.

Between-study heterogeneity was significant (Q(17) = 106.7, and p < 0.001), with I 2 showing that heterogeneity accounted for 84.1% of variation in effect sizes across studies.

Overall between-group analysis (Figure 5).

A significant, small post-intervention between- group total effect size in favour of NMES was calculated using a random-effects model (z(8) = 2.589, p = 0.010, Hedges' g = 0.433, and 95% CI = 0.105-0.760).

Between-study heterogeneity was significant (Q(8) = 18.0, and p = 0.021), with I 2 showing that heterogeneity accounted for 55.6% of variation in effect sizes across studies.


Between-subgroup analyses.

Subgroup analyses (Table 4) were conducted to compare diagnostic groups.

Treatment effects were highest (moderate) for stroke patients, while other groups showed no significant effect sizes.

For all other subgroup analyses, only stroke patients were included to improve homogeneity between studies.


Subgroup anal- yses between studies compared intervention types (NMES, NMES + DT), time between pre- and post-intervention measurement, outcome measures, total stimulation times, elec- trodes configurations, pulse durations, and pulse rates (Table 4).

NMES as an adjunctive treatment to DT showed significant, moderate positive treatment effects, whereas NMES alone showed non-significant effects.


Effect sizes comparing time between pre- and post- treatment measurements showed no clear results.

Although no effects could be identified at 2 weeks, a significant, positive effect size was found at 7 weeks.

When comparing effect sizes based on outcome measures, the only significant effect found was a significant, large effect size for oral intake.

The non-significant effects sizes for visuoperceptual evaluation of instrumental assessment ranged between negligible negative to moderate positive effects.


Total stimulation time subgroup analyses showed significant, moderate positive treatment effects for longer stimulation times (>100 min).

Shorter stimulation times did not result in significant effects.

Comparisons for electrode configurations showed significant, mod- erate positive effects sizes for infrahyoid configuration.

Electrode configuration based on patients' characteristics, including OD outcome scores, indicated non-significant moderate effects, whereas both suprahyoid combined with infrahyoid and suprahyoid configurations resulted in negligible effects.


Final comparisons between studies using different pulse durations did not suggest a linear relationship, whereas pulse rate comparisons indicated that studies using higher frequencies showed increased significant, positive moderate effect sizes.


Five studies using PAS in adult stroke patients were included in the meta- analyses [58,62,65,66,68].

Three studies were excluded from meta-analyses for the fol- lowing reasons: overlap in participant population between studies, insufficient data for meta-analyses, and no confirmation of OD diagnosis prior to treatment.


Overall within-group analysis.

The pre-post intervention effect sizes for the included studies ranged from 0.265 (small effect) [66] to 0.802 (large effect) [62], with an overall moderate effect size of 0.527 (Figure 6).

As one study, however, did not provide PAS data for all included participants [65], a sensitivity analysis was conducted for both PAS and DSRS, indicating minimal differences in effect sizes.


Overall between-group analysis.

A non-significant post-intervention between-group total effect size in favour of PES was found using a random-effects model (z(4) = 0.718, p = 0.473, Hedges' g = 0.099, and 95% CI = −0.170-0.368), suggesting no improvement in PAS outcomes following PES neurostimulation (Figure 7).

Between-study heterogeneity was non-significant (Q(4) = 1.8, and p = 0.766).


Overall between-group analysis.


Between-subgroup analyses.

Subgroup analyses were conducted (Table 4) comparing total stimulation time between studies, favouring shorter stimulation times (z(1) = 0.940, p = 0.347, Hedges' g = 0.300, and 95% CI = −0.325-0.925).


Between-subgroup analyses.


This study (Part I) aimed to determine the effects of PES and NMES in people with OD without excluding populations based on medical diagnoses.

To base findings on the highest level of evidence, only RCTs were included.

This systematic review and meta-analysis were conducted using PRISMA procedures as a guide.


When comparing RCTs in pharyngeal and neuromuscular electrical stimulation (i.e., PES and NMES), various methodological problems became apparent.

Some studies did not define OD or used divergent definitions, whereas other studies applied different inclusion criteria.

Most studies included patients with confirmed OD by instrumental assessment, but several studies used screening, patient self-report or clinical assessments instead.

Consequently, participant characteristics may differ widely between studies.

Despite most studies included stroke patients, meta-analysis comparing diagnostic groups other than stroke was possible for NMES, however this could not be conducted for PES.


Furthermore, the great variety in outcome measures also restricted comparisons by meta-analysis.

As heterogeneity between studies indicates that no estimated overall effect by meta-analysis should be determined, combining studies targeting different domains within the area of OD will have similar implications.

For instance, meta-analyses based on both patients' self-reported health-related quality of life and visuoperceptual evaluation of instrumental assessments would very likely lead to inappropriate estimated overall effects.

Thus, to reduce heterogeneity between outcome measures, some studies were excluded from the meta-analysis.

This strong focus on reducing heterogeneity between studies when performing meta-analysis also implies that data other than the authors' primary outcomes may have been preferably included in this analysis.

For example, the primary outcome for Dziewas, Stellato, Van Der Tweel, Walther, Werner, Braun, Citerio, Jandl, Friedrichs, Nötzel, Vosko, Mistry, Hamdy, McGowan, Warnecke, Zwittag and Bath [59] and Suntrup, Marian, Schröder, Suttrup, Muhle, Oelenberg, Hamacher, Minnerup, Warnecke and Dziewas [64] was readiness for decannulation, which was considered too different from outcomes in the other included studies.


All eight PES studies compared neurostimulation with sham stimulation.

However, among the 30 NMES studies, the comparison group variably consisted of usual care, DT, another dysphagia treatment or a combination of treatments.

In contrast to PES studies that did not include any DT groups, most NMES studies combined neurostimulation with simultaneous DT.

However, DT consisted of a wide range of behavioural interventions, using different treatment dosages, timings, and durations.

Moreover, DT was referred to by many different names and acronyms (e.g., dysphagia training, behavioural intervention, classic treatment, or standard care).

This suggest that care should be taken with the use of DT as an overarching term to group many different behavioural interventions to estimate overall effect sizes in meta-analyses.


Furthermore, RCTs are characterised by random allocation of participants to interven- tion groups and blinding or masking the nature of treatment for participants.

However, in neurostimulation studies, blinding is frequently not feasible and participants may identify what treatment arm they have been assigned to (e.g., the presence of neurostimulation equipment, the experience of active stimulation).

Also, since neurostimulation thresholding in PES is frequently applied in all groups to mask treatment assignment, patients receiving sham stimulation would still have been exposed to a certain level of neurostimulation during thresholding.

Those studies not using thresholding in sham groups (e.g., [59,64]) might show larger treatment effect differences when comparing neurostimulation versus sham stimulation.


When considering meta-analyses for NMES, the highest effect sizes were found for stroke populations.

As existing reviews in NMES [10,12,18,19] excluded other patient populations, no comparisons could be made between clinical populations.

In addition, only two reviews conducted meta-analyses [18,19] selecting studies using different inclusion criteria (e.g., excluding comparison groups with active treatment components [18] or excluding chronic stroke patients [19]).

Reviews may also prefer different outcome data for meta-analyses, especially in the case of RCTs using a large battery of assessments.

As such, total numbers of included studies vary per review, but comparisons between reviews may be falsely estimated due to differences in methodology.


In this systematic review, a wide range in effect sizes was found in NMES RCTs de- pending on outcome measures used.

However, oral intake scales showed highest effects sizes when compared to visuoperceptual evaluation of instrumental assessment or clinical assessment.

This might be explained by NMES treatment usually taking place over consec- utive weeks, in contrast to other neurostimulation techniques (e.g., PES or rTMS) that may be restricted to limited sessions over a few days only.


The great heterogeneity between DT groups also impeded comparisons between NMES only, NMES plus DT, and DT-only groups.

No RCTs provided adequate DT group data to be included in the meta-analysis.

For NMES groups, only two studies were included.

As a result, information about the effects of DT is lacking.

The negligible effect sizes found for NMES without DT were based on only two studies and the moderate effect sizes for combined NMES and DT were based on a total of seven studies.


Most studies performed NMES at motor stimulation level, whereas only a few studies included a group receiving NMES at sensory stimulation level.

As none of these latter studies could be included in meta-analyses, no further details are available on comparisons between effect sizes for sensory versus motor stimulation.

Also, terminology was confusing as sensory stimulation was sometimes referred to as sham stimulation [39].


NMES studies showed marked variation in the technical parameters and protocols applied.

When comparing electrode configurations, both hyoid and combined hyoid and suprahyoid configurations showed negligible effects, whereas infrahyoid configurations resulted in moderate effects.

A study using patient-dependent configurations showed promising results as well [55].

However, it remained unclear which criteria were used to decide on individual configurations.

Furthermore, reporting on many technical parameters proved to be either incomplete or unclear for several studies (e.g., data on pulse duration, pulse rate, or stimulation time).

As technical parameters may depend on medical device manufacturers, comparisons between brands may be warranted.

For example, when considering pulse duration, a clear distinction in effect sizes is found between one study using a lower pulse rate-indicating a negative effect size-versus eight studies using higher pulse rates with moderate effect sizes.


Compared to NMES, fewer PES studies were identified and thus a more limited meta- analysis was conducted.

RCTs included stroke populations, except for one study that included patients with multiple sclerosis [63].

All studies compared active PES with sham treatment in stroke patients and used mostly visuoperceptual evaluation of radiographic recordings of the swallowing act as an outcome measure.

Meta-analysis identified a non-significant post-intervention between-group total effect size in favour of PES.


This finding seemed in line with findings by Chiang, Lin, Hsiao, Yeh, Liang and Wang [19], but this comparison is limited as it is based on only two studies.

Additionally, Bath, Lee and Everton [18] reported that PES studies did not show an effect for many outcome measures (e.g., post-treatment proportions of participants with dysphagia, swallowing ability, penetration and aspiration scores or nutrition).

However, in contrast to previous reviews, Cheng, Sasegbon and Hamdy [7] found a significant, moderate effect size in favour of PES when conducting meta-analysis.


Again, inclusion criteria between reviews differed.

For example, two studies [59,64] were excluded from meta-analysis in this review as well as the reviews by Chiang, Lin, Hsiao, Yeh, Liang and Wang [19] and Bath, Lee and Everton [18], but were included in the review by Cheng, Sasegbon and Hamdy [7].

This may have impacted the overall effect size as both PES studies showed significant treatment effects.


Differences between NMES and PES studies made comparisons between RCTs difficult and hindered meta-analyses.

Studies used different participant inclusion criteria in relation to underlying medical diagnoses or chronicity of stroke and used a large variety of outcome measures covering different domains within the area of OD.

Outcome measures may also lack responsiveness, thus lack sensitivity to change during treatment.

Moreover, studies varied significantly in technical parameters of neurostimulation.

The number of studies and participants restricted the ability of statistical analyses to consider how each variable may have impacted the effects of neurostimulation.


Studies frequently neglected to report on potential moderators of stimulation effects in sufficient detail.

For example, stroke severity and OD severity are inextricably linked and may moderate stimulation effects, yet only very few studies provided data on stroke severity.

Similar problems occur when the chronicity of a stroke is not reported or the possibility of spontaneous recovery is ignored.

This is especially true during NMES treatment, which may span a period of several weeks.

In addition, no consensus was reached regarding the optimal moment for outcome measurement.

Consequently, in this review, between-subgroup meta-analyses were conducted using post-intervention data only, so that the possibility of spontaneous recovery during the intervention period was taken into consideration.


Despite a rigorous reviewing process following PRISMA guidelines and the use of RoB 2 to reduce bias, this review is subject to some limitations.

Only RCTs published in English were included in this current study.

Thus, some RCTs may have been excluded based on language criteria when their findings could have contributed to the current meta- analysis.

Furthermore, meta-analyses included mostly stroke studies, thereby not providing effect sizes for other diagnostic patient populations.

However, the main limitation of this review originates from the high degree of heterogeneity between studies, making comparisons across studies challenging.

As such, generalisations and meta-analyses should be interpreted with care.


Meta-analyses for RCTS in NMES found a significant, large pre-post intervention effect size and significant, small post-intervention between-group effect size in favour of NMES.

For PES studies, the meta-analyses showed a significant, moderate effect size for pre-post intervention, whereas overall between-group analysis did not result in significant treatment effects.

Based on these results, NMES seems to have a more promising outcome compared to PES.

However, only careful generalisations and interpretations of these meta- analyses can be made due to the NMES studies showing high heterogeneity in protocols and experimental variables, including potential moderators, and featuring inconsistent methodological reporting.


There is a need for more RCTs with larger sample sizes in addition to the standard- isation of protocols and guidelines for reporting.

These changes would better facilitate comparisons of studies and help to determine intervention effects more definitively.

Delphi studies involving international experts might allow for a consensus to be reached, thus supporting future research, comparability and generalisability.


We read with interest the authors’ systematic review and meta-analysis of pharyngeal electrical stimulation (PES) and neuromuscular electrical stimulation (NMES) in patients with oropharyngeal dysphagia (OD) [1].

Neurostimulation techniques are increasingly used in the rehabilitation of dysphagia and clearly constitute an emerging field of modern medicine.

Recently, several meta-analyses have been dedicated to this topic, which is also covered in current guidelines [2,3].

As observed by Speyer and co-workers, most of these meta-analyses have focused on specific disease categories, which was the reason why the authors aimed for a wider approach that included any medical diagnoses.

While we appreciate this intention and agree that this meta-analysis adds to current knowledge, we feel that the authors missed their self-set goal of providing the full picture regarding the treatment effects of PES in four respects.


First, the authors excluded two of eight identified randomised controlled trials of PES because they assumed, as stated in the results section, that there was “no confirmation of OD diagnosis prior to treatment” in these studies [4,5].


In our opinion, the exclusion of these studies based on the reasoning put forward by the authors is not warranted.

The two studies in question, a single-centre pilot study [4] and a multicentre trial [5], applied PES in tracheotomised stroke patients who had been weaned from mechanical ventilation but could not be decannulated because of severe dysphagia, a rather common situation in neurocritical care.

Both studies used a well-established FEES-based protocol [6–8] to assess airway safety, a key and fundamental aspect of swallowing function, before and after intervention, i.e., PES or sham.

This protocol consists of a stepwise evaluation of the following three items:


(i) Assessment of secretion: Does the patient present with a massive pooling of saliva or a silent penetration/aspiration of saliva?


(ii) Assessment of spontaneous swallows: Does the patient present with <1 swallow per minute and/or a missing “whiteout”?


(iii) Assessment of laryngeal sensibility/cough: Does the patient have anaesthesia and/or no effective cough upon gently touching the aryepiglottic region with the tip of the endoscope?


If all three items are rated as passed, the patient is considered ready for decannulation; if the patient fails at one or more steps, decannulation needs to be postponed.

While this protocol has specifically been developed for examining tracheotomized patients, all of its items are part of the standard FEES protocol, as recently summarised in an FEES tutorial jointly issued by the American Speech–Language–Hearing Association and by the American Board of Swallowing and Swallowing Disorders [9], and have been found to be of clinical relevance in different areas of dysphagia management.