Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: THE INTERPLAY BETWEEN MOVEMENT, MORPHOLOGY AND DISPERSAL IN TETRAHYMENA CILIATES
Review round: 1
Reviewer: 2

Output:
Basic reporting: This is all fine.
Experimental design: The experimental design is sound and the questions are interesting and well defined.
Validity of the findings: The analyses have serious shortcomings that call the validity of the results into question. Please see my "general comments for the author" for full details on the aforementioned problems and potential solutions to them.
Additional comments: Review of “The interplay between movement, dispersal and morphology in Tetrahymena ciliates” by Pennekamp et al.

This paper uses a tractable lab system coupled with elegant experiments to tease apart relationships between movement, dispersal, genetics, and morphology. I think the questions the authors ask are timely and interesting, and this type of experimental system can help fill gaps between theory and the type of data it is possible to collect under field conditions. So from that perspective, I think this study could be a useful addition to the literature. However, I have some serious issues with the analysis of the movement data that I document at length below. I am signing my review in the interest of full disclosure, as the some of the solutions I propose are based on my own work on movement analysis. I have tried to give careful, objective justifications for the both the problems I raise and the solutions I propose, but wanted to give the authors full information with which to arrive at their own conclusions.

The analyses in this paper are all based on Turchin's 1998 book. To be clear, I think Turchin's book was a landmark in the history of movement ecology and was state-of-the-art for its time. However, huge advances in movement analysis have been made in the 20 years since Turchin's book was published, and none of that progress is leveraged this manuscript. This is especially troubling given that the type of data the authors have collected, with extremely high frequency sampling, represents a worst case scenario for the discrete-time RW methods described in Turchin.

I think the authors would benefit greatly from a shift in perspective about the nature of the data they have collected. The statements about “spurious autocorrelation” (e.g., Ln 181) in the data and the need to remove it, while understandable, are misguided. There is nothing spurious about autocorrelation in movement data. Autocorrelation is a fundamental property of movement data, and the more finely you sample, the more autocorrelation will be revealed. Indeed, any movement process that obeys the laws of physics must feature autocorrelated positions, velocities, accelerations, etc... (E.g., truly uncorrelated positions imply that the animal would be capable of infinite velocity, truly uncorrelated velocities imply that the animal would be capable of infinite acceleration, etc...). The only question is “did you sample finely enough to reveal the inherent autocorrelation in the data”? Furthermore, the precise nature of the autocorrelation in the data contains a wealth of information about the underlying movement process that is being studied. In other words, the movement process leaves a telltale signature in the autocorrelation structure of the data, but decoding that information requires suitable methods.

The discrete-time RW model has a number of severe limitations that render it an inappropriate basis for analysis of high-frequency, highly autocorrelated movement data. This model can only accommodate a very limited form of autocorrelation, and also depends sensitively on the sampling coinciding with behaviorally important events. A consequence of the need to match sampling to behavioral events is that parameter estimates and inferences under this model are highly scale dependent, meaning that if you sample the exact same path at two different sampling resolutions, you will get (potentially very) different parameter estimates. The root of the problem here is that discrete-time RW models confound the (usually arbitrary) sampling process with the underlying (and usually unknown) movement process. In practice, dealing with these limitations means that the investigator must know exactly when to take a sample (i.e., every time the tracked individual makes a movement decision), and if you get it wrong, the inherent scale-dependence of the model guarantees that you will get biased results. In the vast majority of realistic cases including that in the present manuscript, one simply does not know and cannot know the perfect sampling strategy that would result in accurate inferences from this type of RW model. Any time I see statistical methods that only work when the sampling is perfectly right (i.e., require “Goldilocks” sampling, not too fine, not too coarse), I take that as a clear sign that there is something fundamentally wrong.

So the problem here is not your data (which should be good news!), but instead that the model you're trying to use to analyze it is badly misspecified for the data you have. Back when Turchin's book was written, this approach, and the ad-hoc data manipulation it required to shoehorn real movement data into it (like the Douglas–Peucker thinning the authors did), was really the only option. It is also worth noting that the thinning method employed here, if I understood it correctly, would thin each path differently, which when coupled to the inherent scale dependence of discrete-time RWs, would result in *differential* biases among individuals, making any comparisons across individuals or groups hard to interpret. Like I said, however, the game has changed a lot since Turchin's book, and there are now much better methods. The problems with the old approach have also become more apparent given that technologies like the video capture techniques used here, and modern GPS devices, allow for much finer sampling than was possible 20 years ago. The solution is to formally separate the discrete-time sampling process, from the underlying continuous-time movement process that is being sampled. Real animals *always* trace continuous paths through the environment, meaning that the animal had to be somewhere at any given point in time. Turchin acknowledges this fundamental truth at the beginning of the section (5.2.1, pg. 128) on undersampled or oversampled paths.

Continuous-time stochastic process (CTSP) movement models formally accomplish this separation of sampling from movement process, and this is where the link to my own work comes in. While this separation sounds subtle, it changes things fundamentally. CTSPs do not require any ad-hoc manipulation of the data, they naturally handle gaps and missing data, and they do not require matching of the sampling to unknown behavioral processes. Their parameter estimates are scale-independent, with the caveat that to resolve a process operating on timescale tau, the sampling interval must be < tau, which only means that the models are not magic and cannot “see” below the resolution of the data. A key advantage of these models is that they can naturally accommodate arbitrarily autocorrelated data, again with no need to thin or otherwise manipulate the data. A catalog of such models currently exist, and they can be tailored to a give dataset via model selection.

From the description of your data and the sampling frequency you used, I would guess the model that would be most appropriate for your data would be the Integrated Ornstein-Uhlenbeck (IOU) process. This model is also sometimes referred to as the “continuous velocity model” (by Gurarie and colleagues) or the “continuous-time correlated random walk model” (by Johnson and colleagues). The IOU process features autocorrelated positions and autocorrelated velocities (i.e., directional persistence in the movement), and thus should be able to handle your complete datasets. A parameter of this model called the “velocity autocorrelation timescale” can be used to quantify path tortuousity. It measures the typical amount of time it takes for directional persistence (=velocity autocorrelation) in the movement to decay, with a small value indicating a more tortuous path, and a larger value indicating more ballistic-like movement. It is necessarily estimated when this model is fit to the data, and the estimates come equipped with confidence intervals to quantify their uncertainty. A fitted IOU model can also be used as the basis for a scale-independent, and more accurate estimate of movement speed, which is also accompanied by confidence intervals. (Note that summing straight-line distances between location observations and dividing by the total time elapsed, as was done in this study, gives a lower bound on speed, as it assumes the shortest possible travel distance. Additionally, finite difference estimators like this are also highly scale dependent, do not come with confidence intervals, etc...). With those two pieces, you should be able to perform a much more appropriate and robust version of your analysis. I would recommend dropping the diffusion coefficient analysis, as it doesn't contain any information that is not already captured by the speed and tortuousity analyses.

As for how to do this, there are basically two options: the continuous-time movement modeling (ctmm) R package that my lab develops, or the continuous-time correlated random walk library (crawl) R package by Devin Johnson (not affiliated with me or my group in any way). I would recommend using ctmm, but my bias there should be obvious. I do think ctmm has 3 advantages for what the authors want to do relative to crawl: 1) ctmm includes a library of candidate models including IOU, whereas crawl implements only the IOU model. As I said, I would guess that IOU is what you want for your data, but with ctmm, you could formally check if it is indeed best via model selection. 2) both packages will produce velocity autocorrelation timescale estimates and speed estimates, both with CIs, but ctmm's speed() function uses a more sophisticated and accurate estimator than crawl. 3) We frequently use ctmm as a teaching tool in the AniMove movement analysis courses, and we get lots of feedback from students on usability, which we've repeatedly used to refine the interface and workflow. Crawl is definitely functional but is less refined. Either approach, however, would be a substantial improvement over the current analysis, and would allow the authors to make valid comparisons among the different groups in the study. For ctmm, Calabrese et al. (2016, in Methods in Ecology) gives an overview of the package and workflow. The speed() function is available with documentation in the most recent version of the package, but the paper describing the methods behind it has not yet been published (I'm happy to share the ms). Ctmm also has a number of detailed vignettes that walk a new user through how to use it. A full list of papers on the technical methods that ctmm implements can be found at http://biology.umd.edu/movement.html. For the crawl package, Johnson et al. (2008 in Ecology) describes the model and underlying estimation methods. Both packages can be found on CRAN.

Sincerely,

Justin Calabrese


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: THE INTERPLAY BETWEEN MOVEMENT, MORPHOLOGY AND DISPERSAL IN TETRAHYMENA CILIATES
Review round: 2
Reviewer: 1

Output:
Basic reporting: This is fine.
Experimental design: This is fine.
Validity of the findings: See comments below.
Additional comments: I thank the authors for taking my comments seriously and re-doing the analysis based on continuous-time models. I recognize that this was a lot of work, so again thank you. I believe that these efforts will pay off in the long run, as this paper will set a precedent for the analyses of these kinds of datasets.

I am fine with the author's use of the Smoove package and can see that it is setup in a more convenient way for what you wanted to do. I will note, however, that the apparent speed advantage the authors mention as part of their justification for using Smoove over ctmm  (or crawl) comes at a cost. ctmm and crawl implement only exact model fitting methods, which are statistically more rigorous and more reliable, but slower. The default fitting method in Smoove, "velocity likelihood (vLike)", is an approximation that first calculates velocity estimates by differencing the position data, and then treats those estimates as though they were data (i.e., as though velocity had been directly observed by the tracking device). That approach works well when the velocity estimates are good, but can become inaccurate if they are not good. There are many real-world cases where such finite difference velocity estimates can be badly biased, so this is definitely a "user beware" kind of situation, and I believe Smoove should make that clearer to the user. Although I suspect this approximation is ok in your case, given how finely sampled your data are in time, I would like to see an acknowledgement in the paper that an approximate fitting method was used. I would also like to see a spot check on the approximate method added to the appendix. To check if the approximation is ok, you should select a random subset of datasets on which you fitted models via vLike, and do the fit again using the option method='crawl'. This will use the exact likelihood function for the full position data (what Gurarie calls "zLike"), but uses the fast implementation of that likelihood it in the crawl package. Smoove does not implement fast algorithms for the exact likelihood itself, and so has to rely on crawl's fast implementation of this method. (Incidentally, the fast algorithm used for fitting the exact position likelihood in crawl is equivalent to the method ctmm uses for the same model.) You should then compare the two different sets of estimates (exact vs approximate) for each dataset you spot checked. If they differ substantially, you should be concerned, as the exact results are more reliable. I think a small and truly randomly selected subset of your 6072 analyzed trajectories (say, 50 in total) would suffice. This should be added to the supplementary material as a check on the quality of the approximate fits.

Minor comments

There is still mention of "diffusion rates" in the abstract, even though the results on diffusion rates have been removed from the manuscript.

r.m.s. does not stand for "random movement speed" as mentioned on ln 213 in the text. This parameter is the "root mean square" (hence r.m.s) speed.

Also, the "characteristic timescale of autocorrelation" on the next line should be referred to as the velocity autocorrelation timescale, as it specifically relates to the timescale over which autocorrelation in velocity decays. This is an important clarification, as some closely related movement models have multiple autocorrelation scales (position autocorrelation, velocity autocorrelation, etc.).

Sincerely,

Justin Calabrese


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: FEEDING INTENSITY OF INSECT HERBIVORES IS ASSOCIATED MORE CLOSELY WITH KEY METABOLITE PROFILES THAN PHYLOGENETIC RELATEDNESS OF THEIR POTENTIAL HOSTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: This is a clearly written paper of a well-designed and well-executed study to compare the influence of plant phylogeny versus glucosinolate composition on the host plant acceptance of an oligophagous versus a polyphagous herbivorous insect.  The Introduction provides a clear context and rationale for the study.  It would be helpful to include some information about the natural history of the insects, especially C. cardariae (What parts of the plant do adults feed on?  What time of year?  Was the experiment done using 'mature' adults from the preceding year, or young, pre-reproductive adults?).
Experimental design: Methods
The experimental design and analysis generally are appropriate.  However, there do not appear to be any specific methods regarding collecting specimens, extracting DNA, and sequencing the plant material.  How were the plants identified?  Are there voucher specimens?  Provide more description of how a similarity tree was constructed using the GS data.

5 plant samples were used for chemical analysis, which should permit the authors to describe the SE for their mean values.  This would be helpful to show the reliability of the results, and may also help to explain why some compounds were detected in one set of plants, but not in another of the same species (e.g., LD vs. LD2, LC vs. LS2, LS vs. LS2).
Validity of the findings: Results
The authors should check the labeling of Fig. 3 "Glucosinolate dendrogram ... A. Genetic similarity", and "Genetic similarity ... B. Phenotypic similarity".  These labels appear to be contradictory.  Phenotypic trees usually indicate bootstrap levels of confidence.  Adding this to these two figures would help indicate how much confidence can be put on the tree patterns.
Check spelling of C. microcarpus (Fig. 3).

It is surprising to me that H. matronalis and C. microcarpa are mapped as similar on Fig. 3B (phenotype) when the latter has 3 more GS compounds than the former.  Likewise, S. pinnata and L. crenatum are mapped as similar, but differ in the presence/absence of 5-7 compounds.  I encourage the authors to more clearly explain the methods used and the results obtained.

Note that Fig. 4 is not mentioned in the Results section.  Are these data based on all leaves, old leaves, or young leaves?  Do these "young" leaves correspond to "fully expanded leaves in the upper portion ...", which were used in the feeding experiment?  Considering that only young leaves had a significant p-value in Table 3, perhaps the results in Figs. 1 and 4 should focus on the young leaves.  Does C. cardariae normally feed on young leaves?  If yes, then these leaves would probably be more relevant to this study.

Discussion
The plants most similar in the phenotypic tree (Fig. 4) to L. draba and L. campestre (the preferred host plants) had lower levels of feeding by C. cardariae (i.e., B. orthoceras, S. pinnata, L. crenatum) than did D. nemorosa, which is mapped as having a much less similar GS profile.  Fig. 2 shows D.n. as having about the same GS distance from L. draba as at least 4 other plants, which had much lower feeding.  These results appear to be contrary to the conclusion that GS phenotype predicts plant feeding level.  The authors should discuss details such as these.

Visually, the genetic tree (Fig. 3) appears to explain as much of the host acceptability as the glucosinolate 'phenotypic' tree (Fig. 4).  Both trees place L.d. and L.c. in the same clade, and D.n. is remote from this clade in both trees.  This does not appear to fit the conclusion that the GS phenotypic traits can predict feeding preference more reliably than phylogenetic distance.  Neither the phylogenetic nor the glucosinolate trees 'predict' acceptability of Draba nemorosa.

I think that the Discussion could be improved by looking more closely at the results, and less on trying to make a sweeping generalized conclusion.  Can the authors say/hypothesize what compounds C. cardariae likes or does not like?
Additional comments: No additional comments


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: FEEDING INTENSITY OF INSECT HERBIVORES IS ASSOCIATED MORE CLOSELY WITH KEY METABOLITE PROFILES THAN PHYLOGENETIC RELATEDNESS OF THEIR POTENTIAL HOSTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript “Is feeding intensity of insect herbivores associated with phylogeny or glucosinolate profiles?” tackles an important question in ecological interaction between Brassicaceae plants and their specialized herbivores. The main question in this manuscript is whether the phylogenetically disjunct host range of Ceutorhynchus cardariae can be associated with glucosinolate (GS) profiles of its host plants. This question is important since C. cardariae is an important candidate for biological control of global-invasive plants, Lepidium draba, and understanding the factor which limits its host range would be beneficial to control non-target effect in such biological control. The author performed feeding experiments (including Plutella) and genetic analysis coupled with chemical analysis. It was interesting to see that C. cardariae responded more sensitively to GS profile differences of their hosts than Plutella. However, there are several points which need to be considered before publication.

The major points of criticisms
1.	The author compared the results of feeding assays of C. cardariae and P. xylostella as their one of the main results. However, these two species can be different in many ecological aspects although both of them are Brassicaceae specialist. The author should at least explain that the way of feeding can be different between weevils and caterpillar and how this difference can affect the results of your feeding assay. For example, leaf toughness or trichome density can affect differently to these two species.
2.	The explained experimental setting was confusing. Please clearly state how many individuals of C. cardariae and P. xylostella the author used for feeding experiments in the Material & Methods section. I assume it would be 5 from tables and raw data sets, however, it would be more useful for readers to be explained at MM section.
3.	Why the author only used females of C. cardariae for the experiments? (l. 168)
4.	What is the rearing condition of C. cardariae laboratory strain (l. 118). Were they reared on plants or an artificial diet? If plants were used, which plants? How this can affect the difference you found between P. xylostella larvae which were reared on artificial diet before the feeding assay?
5.      Why did the authors use p-distance to estimate genetic distance? This p-distance only shows the number of nucleotide changes and does not reflect transversion-transition differences or cases of multiple substitutions (l. 227).  In addition, in the ndhF sequences used in this study, there are a number of ‘N’. How did you calculate genetic distance from these sequences? If you removed such sites, please state it. You should also explain the final sequence length (bp) you used for your analysis.
6.	In the manuscript, the authors explained that GS profiles of Brassicaceae are not phylogenetically conserved evident from your data sets (l. 333-). It is difficult to say this since there is no test in this manuscript addressing this point. Furthermore, I also believe that it would be difficult to test this in this dataset since there was no solid plant phylogeny provided in this manuscript. I would suggest rephrasing this such as; GS profiles can vary even among closely related species.
7.	The motivation of this research is giving important information to estimate the non-target effect of C. cardariae that has phylogenetically disjunct host range but seems to respond differently depending on the GS profiles of plants. It would be more beneficial if you can point out which GSs can be candidates that would affect the feeding behavior of C. cardariae according to your results. This information would be quite important when one would design biological control of L. draba by C. cardariae practically.

Minor comments
l. 67.　There are several studies focusing on herbivore host ranges associated with plat leaf traits or phylogenies although these are more community ecology based.
Nakadai, R., & Murakami, M. (2015). Patterns of host utilisation by herbivore assemblages of the genus Caloptilia (Lepidoptera; Gracillariidae) on congeneric maple tree (Acer) species. Ecological Entomology, 40(1), 14–21. doi:10.1111/een.12148
Volf, M., Hrcek, J., Julkunen-Tiitto, R., & Novotny, V. (2015). To each its own: differential response of specialist and generalist herbivores to plant defence in willows. Journal of Animal Ecology, n/a-n/a. doi:10.1111/1365-2656.12349

l. 146 Which stage of plants did you use for the feeding experiments? What was the condition of the greenhouse for rearing?

l. 241 Please add the name of the statistical test you used to get the P value (P > 0.05).
l. 270 Maybe original 43?
l. 288 P should be italicized.
l. 343 What are these normalized feeding intensities? How did you measure these?
l. 355 What does this sentence mean? There is a recent publication about Plutella GSS. You may include this information to discuss this.
Heidel-Fischer, H. M., Kirsch, R., Reichelt, M., Ahn, S.-J., Wielsch, N., Baxter, S. W., Heckel, D. G., Vogel, H., Kroymann, J. (2019). An insect counteradaptation against host plant defenses evolved through concerted neofunctionalization. Molecular Biology and Evolution, 36(5), 930-941. doi:10.1093/molbev/msz019.
l. 357 For example which GS?
l. 360 In this paragraph you may also include some information about the plant species you used for this study and how this can affect your results. For example, Stanleya is known to be toxic by accumulating Se and Brabarea is known to have saponins.
l. 381 remove “profile” before GS
In file “peerj-38348-Rapo_et_al_SUPPLEMENTARY_TABLES.docx”
There are “3rd pop” in Lepidium latifolium. Maybe this should be 2nd?
Experimental design: Some experimental methods should be explained more clearly. See basic comments.
Validity of the findings: no comment
Additional comments: no comment


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: FEEDING INTENSITY OF INSECT HERBIVORES IS ASSOCIATED MORE CLOSELY WITH KEY METABOLITE PROFILES THAN PHYLOGENETIC RELATEDNESS OF THEIR POTENTIAL HOSTS
Review round: 1
Reviewer: 3

Output:
Basic reporting: Clear and unambiguous, professional English used throughout. --> yes, but in my opinon, some areas require rewording for clarity.

Literature references, sufficient field background/context provided. --> Some important work that provides context to the study is missing; I provide some references in the section below.

Professional article structure, figures, tables. Raw data shared. --> Article structure seems good. Find some comments in the section below.

Raw data is not shared, but this can be easily fixed.

Self-contained with relevant results to hypotheses. --> yes
Experimental design: Original primary research within Aims and Scope of the journal. --> yes

Research question well defined, relevant & meaningful. It is stated how research fills an identified knowledge gap. --> yes

Research question --> yes

Rigorous investigation --> yes

Methods described with sufficient detail & information to replicate --> no; but easily fixable. Some suggestions provided below.
Validity of the findings: no comment
Additional comments: ++++++++++ Overview
In this paper, the authors assess whether feeding intensity of a specialist and a generalist feeding on mustards is best explained by genetic distance of potential hosts to true host, glucosinolate profile distance of potential hosts to true host, or total glucosinolate concentration in potential hosts. They find support for chemical distance and glucosinolate concentration being important predictors of feeding intensity, and little if no role of genetic distance.
I find the manuscript interesting and generally well written. However, references to important pieces of literature, and some information on methods and results are lacking.
My biggest issue with this paper is the use of genetic distance phylograms instead of trees derived from proper phylogenetic analyses, which could be easily, inferred using the available genetic information (or derived from the work of others). Today phylogenetic analyses are common; literature and resources to conduct such analyses is plentiful, as is the literature on comparative methods. While this implies that some downstream analyses would need to be repeated, it might be worthwhile given the strong emphasis of this paper on phylogenetic relatedness.
Below and in an accompanying PDF I offer detailed comments and suggestions as to how, in my opinion, some of the issues can be addressed.

+++++ Detailed comments

INTRODUCTION
L 65-66. In Asclepias, phylogenetic signal varies in the many defensive compounds it produces. While stronger for cardenolides, it is moderate for flavonoids, and low for phenolics (Agrawal etal., 2009). In fact, weak phylogenetic signal in secondary metabolites associated with defense has been reported in various systems, including terpenes in Bursera (Becerra etal., 2009), tannins in oaks (Pearse & Hipp, 2009), flavonoids in evening primroses (Johnson etal., 2014), phenolics in Inga, alkaloids in Datura (Karinho-Betancourt et al., 2015), and importantly for this paper, in glucosinolates in Streptanthoid mustards (Cacho et al., 2105).
Given the above, while I agree that “total cardenolide concentration in Asclepias is a factor accounting for the range of T. tetraphthalmus” I find complicated to qualify it as a “phylogenetically constrained”  host range.  Evidence is that phylogeny plays a rather weak role in defensive secondary compounds. I think this is the case as well in Bursera. In my opinion, including this discussion and references builds on the discussion of phylogeny vs. chemical similarity in predicting host ranges, and thus provides an important context to this study.
L 70-83. Classic examples of this very phenomenon in Bursera (work by Becerra and collaborators), which should be addressed here.
L 89-91. Glucosinolates have been shown to exhibit low phylogenetic signal (work of Cacho and collaborators) should be addressed here.
L99-102. Given the above [and your results], this is quite surprising. Chemical similarity and not phylogenetic relatedness should be the standard for this practice.
L 107-114. I do not follow the rationale under which the expectations are the same for a specialist and a generalist herbivore. If specialization does not play a significant role in the hypothesis then maybe this should be clarified and less emphasis placed on it.

METHODS
Insect section. Please make clear that female weevils are being used (and why).
L 168. Need to explain why where weevil females starved but Lepidoptera larvae were not.
L. 178. Comma between image and which is not needed; please remove.
L 192 -193. A justification or reference is needed for the criteria used to classify leaves in this way. Are both young and old leaves cauline or are “old” leaves a mix of cauline and basal leaves? Please clarify. Also, provide details on how were nodes counted in plants that have basal rosettes?
Genetic phylograms and glucosinolate dendrograms–
Given the strong emphasis put on phylogeny in this paper, I am surprised that not proper phylogenetic analyses are used in this paper. Please explain/justify why this choice was made.
Regardless of the choice of method, the alignment methods and parameters need to be included.
The Genbank numbers for ndhF sequences are provided, but in needs to be explicit if these sequences were downloaded from Genbank or generated for this study.
If proper phylogenetic analyses were not implemented, then all references to “phylogenetic relatedness” should be replaced with “genetic similarity” or something similar. The same is true for figures. References to “phylogenetic” should be replaced with “genetic”.
L 2454 – 247. I find this confusing. Here is a suggestion:  For C. cardariae and P. xylostella separately, we evaluated feeding intensity as a function of genetic similarity to L. draba, chemical similarity to L. draba, and total GS in leaf tissue.
Please provide details on how were genetic and chemical distances to L. draba calculated.
Were differences between young and old leaves significant? If so, I expect separate analyses for these two different kinds of leaves.
Were assumptions of normality tested before linear models?
L. 248-260. This is an interesting idea (although the writing is a bit confusing). Phylogenetic signal is the tendency of related species to resemble each other more than species drawn at random from the same tree. Assessing whether mathematically the methods to measure degree of resemblance by different tips of a dendrogram is beyond my expertise. Has anyone implemented this approach? If so, please cite.
Suggestion: “… can work with dendrograms based on other information…” should read “…can work with dendrograms.”  Please provide the number of permutations to test significance.
As far as I know, kappa is not a measure of phylogenetic signal. Literature is vast on the topic.
L. 257-259. I find this confusing. Here is a suggestion: “We calculated Blomberg’s K for feeding intensity using our genetic and chemical dendrograms in lieu of phylogenies.”
Please provide details on libraries and functions for analyses done in R.

RESULTS
L 269-270. How were the 26/43 glucosinolates selected to be retained for analyses? Please explain criteria (if these are different from only curating the GS results, see below).
L. 270. Were there 43 or 45 GS or compounds?
L 270-275. These should be in methods as GS post-HPLC curation.
L. 285-288. I had not understood the multiple regression part from the methods section. Please provide a table with the full model with the effects (coefficients, SS, P-values) for the different factors.

DISCUSSION
L 330. I suggest that the following more cautious formulation is used: “…concentrations among the plant species tested, consistent with the hypothesis that glucosinolates stimulate feeding in C. cardariae.”
L 334. Include additional references supporting glucosinolates not showing strong phylogenetic signal, and also references that this pattern is not exclusive to glucosinolates but rather secondary defensive compounds (see comments on introduction).
L 343-344. Please provide details in methods as to how these normalizations were performed.
L. 372. “and if they are phylogenetically labile”

FIGURES AND LEGENDS
Table 2. The values for the ANOVA and KW tests should go in the legend, not as part of the table.
Fig. 1. It would be good to add a row for total GS per species.
Fig. 2. The symbol for mole is “mol”, so units should be expressed as “µmol/g”. It is best if significance is indicated in the graph panel.
Figs. 3 and 4. Make sure the figure legends are correct; seems to be switched, stating that figure 3 is glucosinolate dendrogram and figure 4 is genetic …
Table S1.  The title for this table would be best to include “experimental design” in it, and highlight the five block used and referred to in the main text. This will help the reader focus on the main information of this table. Also, the date needs to include year.
Figs. S1. Are both young and old leaves cauline or are “old” leaves a mix of cauline and basal leaves?
+++


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: FEEDING INTENSITY OF INSECT HERBIVORES IS ASSOCIATED MORE CLOSELY WITH KEY METABOLITE PROFILES THAN PHYLOGENETIC RELATEDNESS OF THEIR POTENTIAL HOSTS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have undertaken a careful and substantial revision, addressing all major concerns.

There are only small corrections should be done.

Minor comments
Line: 248 Throughout: ndhF should be italicized.
Line: 303 remove "with"
Line: 424 "disjunct"
Table2 column name "Total GS (nmol/g)*" might be µmol/g? In addition, what is the meaning of "*" shown here?
Experimental design: OK
Validity of the findings: OK
Additional comments: No additional comments


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: FEEDING INTENSITY OF INSECT HERBIVORES IS ASSOCIATED MORE CLOSELY WITH KEY METABOLITE PROFILES THAN PHYLOGENETIC RELATEDNESS OF THEIR POTENTIAL HOSTS
Review round: 3
Reviewer: 1

Output:
Basic reporting: ok
Experimental design: ok
Validity of the findings: ok
Additional comments: No additional comments


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: GENETIC AND SEROLOGIC SURVEILLANCE OF CANINE (CIV) AND EQUINE (EIV) INFLUENZA VIRUS IN NUEVO LEÓN STATE, MÉXICO
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment'
Experimental design: no comment
Validity of the findings: no comment
Additional comments: This study unveil the incidence of the Influenza A virus in the horse and dog population of the state of Nuevo León. As well as the impact of the absence of vaccination on these animal populations. This study suggests the constant detection of influenza virus in animal companion in order to investigate its epizootic and zoonotic potential. However, the manuscript needs to be further reorganized and revised, especially the section of “Discussion” and “Introduction”, before publication.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: GENETIC AND SEROLOGIC SURVEILLANCE OF CANINE (CIV) AND EQUINE (EIV) INFLUENZA VIRUS IN NUEVO LEÓN STATE, MÉXICO
Review round: 1
Reviewer: 2

Output:
Basic reporting: The language is clear and professional.
But no sufficient field backgroud is shown in Introduction and discussion.
Experimental design: Is M gene suitable for analysis of virus typing?
Validity of the findings: No significant finding was shown.
No comparision among this studies and other published reports.
Additional comments: In this manuscript, the authors performed a surveillance of canine (CIV) and equine
(EIV) influenza virus in Nuevo Leon State, Mexico. Due to analyze the M gene, they considered H1N1 is the major type which is pandemic in this area in dogs and horses. At the same time, higher positive rate in the serological results was shown. However,
1) Not specific and no relative conclusion was conluded.
2) The time about harvesting these samples was not shown, and it is improtant for surveillance of virus.
3) Much information (ex. viral type et., al) in only one figure is absent.
4) No significant finding was shown, and no comparision among this studies and other published reports.
5) Is M gene suitable for analysis of virus typing?


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: GENETIC AND SEROLOGIC SURVEILLANCE OF CANINE (CIV) AND EQUINE (EIV) INFLUENZA VIRUS IN NUEVO LEÓN STATE, MÉXICO
Review round: 1
Reviewer: 3

Output:
Basic reporting: In this manuscript “Genetic and serologic surveillance of canine (CIV) and equine (EIV) influenza virus in Nuevo Leon State, Mexico” by Plata Hipolito et al., the authors evaluated the presence of CIV and EIV in dogs and horses, respectively, from samples collected in 9 municipalities in the state of Nuevo Leon in Mexico using RT-PCR approaches targeting the matrix (M) viral segment. Authors identified the presence of CIV and EIV in several of the analyzed samples, demonstrating the incidence of these viruses in the horse and dog population.
Experimental design: Overall, the experiments are well designed but the authors should include the results from their serological studies.
Validity of the findings: This is the first genetic and serologic study conduced in Mexico to detect the presence of CIV and EIV in dogs and horses, respectively.
Additional comments: In this manuscript “Genetic and serologic surveillance of canine (CIV) and equine (EIV) influenza virus in Nuevo Leon State, Mexico” by Plata Hipolito et al., the authors evaluated the presence of CIV and EIV in dogs and horses, respectively, from samples collected in 9 municipalities in the state of Nuevo Leon in Mexico using RT-PCR approaches targeting the matrix (M) viral segment. Authors identified the presence of CIV and EIV in several of the analyzed samples, demonstrating the incidence of these viruses in the horse and dog population.

Overall, this manuscript describe the first attempt to detect the presence of CIV and EIV in Mexico and demonstrate the presence of both viruses in the dog and equine populations in several parts in the state of Nuevo Leon in Mexico. There are, however, some general and specific comments that the authors should consider to improve the quality of the manuscript:

General comments:
-	After completing the reading of the manuscript, I am not sure what type of CIV or EIV they have identified in this study. Are these CIV H3N8 or H3N2 and EIV H3N8? These are the most common influenza viruses circulating in dogs and horses, respectively; but based on how the manuscript is written, I am not sure what subtypes of influenza viruses they have found. The authors should carefully revised the different sections of the manuscript, including the title, to clearly state what subtype of viruses they have found circulating in dogs and horses.
-	The authors indicate and describe conducting some serological studies. However, these data has not been included in the manuscript. The authors should relevant data related to the serology studies in the manuscript.
-	Likewise, the authors should provide evidence that the M protein purified from bacteria was produced in sufficient quantity and quality to conduct these serological studies.
-	For detection of CIV and EIV, the authors used RT-PCR-based approaches with specific primers targeting the M viral segment. However, it is unclear what subtype of influenza A virus is the target of these primers and whether or not will bind to conserved sequences in H3N8 and H3N2 CIVs, or H3N8 EIV.

Specific comments:
-	Please, revise the entire document to clearly state what type of CIVs or EIVs have been identified in this study.
-	Please, use the proper nomenclature for the H1N1/2009 influenza A virus. Moreover, it will be important to indicate the origin/source of this H1N1/2009 virus.
-	Please, clarify the nature of the primers used for the amplification of the viral M segment and whether or not these primers match the sequence of H3N8 and H3N2 CIVs; and H3N8 EIVs.
-	Include the results for the serological studies described in the manuscript. Moreover, provide the results related to the purification of the M1 protein used to detect the presence of CIV and EIV antibodies in dogs and horses, respectively; including quality and quantity of protein preparation.
-	Table 1. It is unclear why the authors include some municipalities (e.g. Monterrey, Escobedo, Apodaca and Guadalupe) since samples from these regions have not been used in the study.
-	Table 2. The authors should be able to combine Tables 1 and 2 in a single Table. There is redundancy on the information currently provided in Tables 1 and 2.
-	Table 3. To me, this is more a Figure than a Table. It will be important to include the name of the viruses used in this amino acid alignment, rather than the reference number. Also, please, include the subtype of viruses (e.g. H1N1, H3N2, H3N8). Finally, include a complete sequence of the M viral coding region.
-	Figure 1. Change the accession number but the name of the influenza strains used in this phylogenetic analysis. As indicated above, also include the subtype of viruses (e.g. H1N1, H3N2, H3N8).


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: GENETIC AND SEROLOGIC SURVEILLANCE OF CANINE (CIV) AND EQUINE (EIV) INFLUENZA VIRUS IN NUEVO LEÓN STATE, MÉXICO
Review round: 1
Reviewer: 4

Output:
Basic reporting: Overall an interesting study that seeks to define the prevalence in Mexico of influenza A virus in dogs with respiratory disease or (serology) in stray or feral dogs. Also in trash-collecting horses. The data is based on a nested PCR of the M gene of the influenza viruses, as well as an ELISA based on using a recombinant M1 protein expressed in bacteria. The results are surprising as they report a quite high prevalence of viral RNA, which match the sequence of the human H1N1pandemic virus, and about 100% serological +ves. As mentioned below, these results suggest that there may be contamination in the samples, or cross-reactivity. There is a need for additional controls to ensure that the results are an accurate reflection of the infection status in Mexican animals.
Experimental design: Main issues are technical - to ensure that the results are accurate.
Validity of the findings: One issue is that the proportion of positives in the serology (or stray dogs) is much higher than has been reported in any other region of the world - where the proportion of +ves tends to be <5%, except in outbreaks or infected colonies. I suggest that an independent test of the sera with a different ELISA test should be carried out to confirm the results seen here with the E. coli-expressed protein.
The high number of +ve PCR results is surprising, even in dogs with respiratory disease, unless there is a major outbreak going on. Human viruses generally do not spread in dogs.  To find such high levels in the absence of a documented outbreak seems unlikely. What was the situation in the human population, as this appears to be a human H1N1pandemic virus? Can other sequences be obtained to confirm the origins and serotype of the virus, and to confirm that this was not due to contamination?
In Figure 1, I am not sure what the sequences are that are included - what are the different labels referring to? Such as Zoontic reassortants - of what virus strain? What are contemporary strains? What are ancestral strains - those were from H3N8 viruses in horses, or dogs? What are the outgroup viruses?
Additional comments: No additional comments


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: GENETIC AND SEROLOGIC SURVEILLANCE OF CANINE (CIV) AND EQUINE (EIV) INFLUENZA VIRUS IN NUEVO LEÓN STATE, MÉXICO
Review round: 2
Reviewer: 1

Output:
Basic reporting: This manuscript is difficult to follow in places, and needs to be edited carefully for English usage. The overall presentation appears to be reasonable.
Experimental design: The experimental design is seeking to detect the presence of influenza viruses in horses and dogs in Mexico. The design of the studies seems reasonable, and the revision addresses many of the comments about the studies. A concern is whether the controls for -ve samples are rigorous enough to exclude possible false positives.
Validity of the findings: The results have not changed, and show >90% +ve sera in both horses and dogs, and about 5-20% viral RNA +ves by PCR. The numbers are still much higher than have reported for previous studies for dogs. The +ve PCRs still seem to be much higher than have been reported for other studies for influenza hosts, and imply active infection or persistent virus in a relatively high proportion of the animals. The proportion of canine serum +ves are also very high compared to other populations that have been examined.
Additional comments: No additional comments


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: RESOLUTION-AGNOSTIC TISSUE SEGMENTATION IN WHOLE-SLIDE HISTOPATHOLOGY IMAGES WITH CONVOLUTIONAL NEURAL NETWORKS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The reviewer agrees that the automated tissue detection in the scanning software has drawbacks, but the authors need to articulate them properly. Please provide specific examples showing circumstances that make scanners fail to detect tissues on slides. For instance, you can illustrate how the automated tissue detection works in Aperio and Pannoramic scanners. The statement made: “Unfortunately, there is no way to recover from errors made in tissue detection by slide scanners”, seems to be groundless. For instance, in user interface of Aperio scanning software, one can inspect and, if necessary, correct the bounding box drawn over the detected tissue. Once the tissue is inscribed in the bounding box, the scanner proceeds with scanning of area inside the bounding box. Software from other scanner manufacturers may have built in similar feature.

The authors say that “The typical file size of a WSI was around 4 GB, but it varied greatly depending on the scanner and tissue content of the image.” True, but this needs to be amended that the file size also depends on the scanning magnification (20x or 40x set manually in Aperio).

Example ground truth delineations need to be shown in a separate figure to give readers an idea on how they were made. Illustrate how experts annotated areas that have holes, normal lung parenchyma, or areas with adipocytes.  Amend your manuscript with criteria your experts used while circling the tissue and separating it from background. These criteria are important to understand errors made by CNNs.

Image augmentation technique described in the manuscript seems to be overlapping in some parts with that described by Tellez at al (https://arxiv.org/pdf/1902.06543.pdf). Please list shared procedures, if there are any, and reduce the section volume if possible.  Also, state what's new in your augmentation approach as compared to that by Tellez et al.

Inference section: explain the notion of the confidence value t. Is it the same as probability score outputted by CNN?

Ln 248. Explain what you meant by post-processing of measurements. Did you mean a post-processing of the resulting binary tissue mask?
Experimental design: Explain if and how a result obtained by CNN is affected by tissue thickness. A typical thickness of tissue re-cut for a histopathological evaluation is 4um. However, 3um or 5um sectioning is not uncommon. Include information about tissue sections included in the study. In If the slides (Table 2) are all 4um, the authors should collect slides that are 3um thick and analyze them with their CNNs and report performance.  The performance should be evaluated statistically to identify potential differences arising from thicker vs. thinner tissue sections.
Validity of the findings: In introduction, the authors listed only most commonly used techniques for tissue detection. However, as shown for instance in https://www.ncbi.nlm.nih.gov/pubmed/25372389 or https://www.ncbi.nlm.nih.gov/pubmed/30728398 , a miniature RGB image of the whole WSI (say at the level equivalent to 5x) converted to a monochromatic image and then thresholded using a fixed intensity value seems to work sufficiently well to separate tissue from background. Please implement this simple technique, include its performance in Table 6, and discuss.

Methods section: clarify how exactly the Otsu reference method was applied to delineate tissue. WSI images are RGB matrices and the Otsu method works in principle on monochromatic images only.
Additional comments: No additional comments


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: RESOLUTION-AGNOSTIC TISSUE SEGMENTATION IN WHOLE-SLIDE HISTOPATHOLOGY IMAGES WITH CONVOLUTIONAL NEURAL NETWORKS
Review round: 1
Reviewer: 2

Output:
Basic reporting: This paper applied a fully convolutional neural network-based approach to segment/distinguish tissue versus non-tissue on tissue glass slides. It's overall well-structured and written. However, it lacks background introduction with enough reference and discussion of the state-of-the-art methods tackling the same question (the author mentioned two general segmentation methods, but how do people distinguish tissue versus background currently, how significant is this problem? Whether the reasonable missing of the tissue is acceptable in the clinic? The author should either provide literature evidence or self-generated data to support the current scanner has a high rate of failing to detect tissue and this really affect diagnostic accuracy).
Experimental design: The author applied a fully convolutional neural network to segment the tissue from the background on a pathology slide. The data and model were described with details.

However, the author mentioned in the introduction at line 48-50 the scanner could miss the tissue during the scanning. It looks the author aims to solve the missing-detection of the scanner. But I couldn't see how the proposed approach could solve this issue. Your approach and application are built upon after the image acquisition. Based on my understanding, the proposed resolution-agnostic network could scanner the at low-resolution to guide the scanner. But the author should explicitly describe how you would image happen and embed within the scanner itself. The fundamental transition and assumption should be provided.
Validity of the findings: The author provided a fully convolutional neural network-based approach to address the tissue segmentation problem on digitized tissue slides. The author compared with thresholding and structure detection approaches and stated the single FCN is multi-resolution enabled as well. Considering the previous evidence of deep learning-based approaches in image segmentation and classification, the result is not surprising. However, the author should state or compare why to choose the FCN rather U-Net or GAN based approach as they recently surpassed the FCN.
Additional comments: The overall paper is well-written with supportive table and data. However, the author should provide more background with reference/own data regarding why the problem addressing is significant. Also, the author should compare with more state-of-the-art approaches.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: RESOLUTION-AGNOSTIC TISSUE SEGMENTATION IN WHOLE-SLIDE HISTOPATHOLOGY IMAGES WITH CONVOLUTIONAL NEURAL NETWORKS
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: no comment
Additional comments: Thank you. The authors addressed all my comments properly.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: RESOLUTION-AGNOSTIC TISSUE SEGMENTATION IN WHOLE-SLIDE HISTOPATHOLOGY IMAGES WITH CONVOLUTIONAL NEURAL NETWORKS
Review round: 2
Reviewer: 2

Output:
Basic reporting: The author has sufficiently addressed previous issues.
Experimental design: The author has sufficiently addressed previous issues.
Validity of the findings: The author has sufficiently addressed previous issues.
Additional comments: The author has sufficiently addressed previous issues.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: WHY DO WE TRANSITION FROM WALKING TO RUNNING? ENERGY COST AND LOWER LEG MUSCLE ACTIVITY BEFORE AND AFTER GAIT TRANSITION UNDER BODY WEIGHT SUPPORT
Review round: 1
Reviewer: 1

Output:
Basic reporting: Language can be improved. I have made numerous suggestions. Key references are missing as noted. Otherwise OK
Experimental design: Method of RGS is not described with adequate detail.
Validity of the findings: Data are OK, but I can't understand why they find faster PTS in RGS. It contradicts numerous previous findings but strong researchers.
Additional comments: 1.	Overall, this manuscript reports new evidence that whole-body metabolic energy is not the sole trigger for the walk-run transition in humans. Rather they find that local factors (muscle activity) play at least some role. That is not a particularly new finding for normal gravity, but PeerJ specifically does not require novelty for publication. Rightly, PeerJ recognizes that replication is an important part of science. With regard to normal gravity, this study mostly replicates the previous findings of other groups: Hreljac, Prilutski, Neptune etc. The authors should do a more thorough job of citing the studies that are being replicated.

2.	The simulated reduced gravity (SRG) findings are potentially novel but the critical finding that the Preferred Transition Speed is faster than in normal gravity (NG) is the direct opposite of what has been found by the Cavagna lab group, the Minetti group, the Ivanenko group and the Kram group. The authors do not recognize that contradiction, reference those papers or explain why they have found the opposite trend. In contrast, the previously reported reduction in the PTS in SRG does have a theoretical basis (Froude number).

3.	All of the above studies have used at least slightly different methods of body weight reduction, but the finding of slower walk-run transition speeds is consistent in those studies. The present study uses yet another apparatus. The present authors do not provide key information about their SRG apparatus that might allow a reader/reviewer to compare the new device to previous devices. I would like to know the mass of the rigid frame + sliding part. Further, it would be helpful to have a graph of the applied force vs. time. Further, the device as depicted probably allowed the person to “hang back” allowing the harness to pull forward as well as up. The spring is quite short (only 30cm) and thus I suspect that the 3-4 cm of vertical movement by the person would cause a large amount of force fluctuation. The spring constant of 5.7 kg/cm suggests that a 3 cm movement would change the force by almost 20kg!

4.	On line 140, it states that the acceleration of the treadmill speed was 1.67 m/sec^2. That is amazingly fast and I think in error. If the initial speed was 1.11 m/sec, the treadmill speed would be > 2 m/sec in less than 1 second!

5.	I don’t see any problems with the EMG or metabolic energy measurement methods. However, I am not an at interpreting MPF. The statistics seem OK.

6.	Line 67 Why would I expect this change in EOTS since the met cost of both walking and running are reduced in RGS? In general, the logic from lines 67-70 is confusing

7.	L141 how was the gait detected/quantified?

Minor Comments/Suggestions
Line 1 Title: Why do we transition  (not transit)
L17 energetic cost of transport
L18 literature (no s)
L19 argues
L20 cut: “the”
L21 body weight  (not body mass)
L22 muscle activity  (you do not measure work)
L24 I suggest you are consistent and use “s” for speed rather than using both s and v
L26 during constant acceleration protocol (i.e. velocity ramp)
L26 1.67 can’t be correct
L28 using electromyography of the primary ankle dorsiflexor
L29 after the walk-run transition
L31 both were faster under SRG than in NG.
L31 In both gravity levels, MPF decreased after the walk-run transition in the dorsiflexors and the combined plantar flexor activities, especially the soleus.

L34 The walk-run transition is not triggered solely by the minimization of whole-body energy expenditure.
L35 Gait transition is associated with reduced TA and soleus activities with evidence of greater slow twitch fiber recruitment perhaps to avoid….
L38 Human terrestrial locomotion
L39 it would be nice to cite some of the original studies (Margaria) rather than these citatiosn which are reviews of review papers.
L44 energetic
L44 s instead of v
L45 approximately linear
L50 Ziv is for racewalking, a very different gait
L51 explain the trigger for the walk-run transition
L53 should cite the Hreljac classic paper on this
L55 becoming
L58 I suggest using MG and LG.  GM is often used for Gluteus maximus.
L64 muscular activity but also the required…
L67 muscular activity, it
L68 would be faster in SRG
L70 would be faster in SRG compared to NG.

L70 flexor (no s)
L70 decrease after the transition from walking …
L73 investigate the muscular activity and the motor unit…
L74 flexors
L74 under NG and SRG conditions.

L77 To determine…
L79 measurements
L92  & L98 body weight (BW)
L98 spring system.
L98 The set-up allowed normal leg swing.
L103 on a level…
L104 After measuring the mLetabolic cost of walking…
L105 Cut “running”
L105 with 1 min standing rests between the running stages.
L106 At all stages…
L107 and the same model of shoes in the appropriate sizes.

L109 dots over VO2 and VCO2
L111 Calibrated gas concentrations
L114 and 115  “s” instead of v
L134 to allow placement of the pre-amplified…
L137 The electrode leads were secured…
L140 increased at an acceleration of xxx
L142 throughout
L145-6 artifact in the EMG
L151 A foot sensor
L155 Subsequently, a fast Fourier…
L159 normalized to

L177 at all speeds
L178 significantly faster
L181 significantly slower
L182 the combined plantar flexor
L185 combined plantar flexor
L189 under both gravity conditions
L192 MG
L194 LG
L203 The results also demonstrated that the EOTS was faster in SRG than in NG
L210 significantly slower
L211 These results indicate that the walk-run transition is not triggered exclusively to minimize whole-body EE.
L213 I would move this sentence later in the paragraph. State your own results and then put in context.
L220 fibers after the gait transition.
L222 cut: “which are the antagonists of the TA”
L225 for the walk-run transition
L229 the combined activities
L231 cut “should”
L231 contribute to triggering the gait transition. Cut “in some way”
L240 In fact, the gastrocnemius…
L242 cut “muscular activity of the”
L244 of our experimental approach was that we could not quantify in vivo…

L248, L250 what is “shortening length”? and how does it “recover”?
L255 required forces, in association…

L260 was significantly slower
L260 …indicating that the walk-run gait transition is not only triggered by the minimization of whole-body EE. In the SRG…
L262 and EOTS were faster


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: WHY DO WE TRANSITION FROM WALKING TO RUNNING? ENERGY COST AND LOWER LEG MUSCLE ACTIVITY BEFORE AND AFTER GAIT TRANSITION UNDER BODY WEIGHT SUPPORT
Review round: 1
Reviewer: 2

Output:
Basic reporting: This study is well presented in terms of article structure, literature references and background provided. However, I think that authors  would be to attend a some aspect for future submission:
1) Caption of figure 3 is poor and it not include a sufficient description of the illustration.
2) Table with physical characteristics of participants should be included in Participants subsection.
Experimental design: The experimental design is well defined in accordance with the research questions to be addressed by the authors. It was performed with high technical and ethical standards.
It is clear that much work has taken place, but some technical points are not clear in the current version of the manuscript and the authors would to attend the comments included in the document attached before submitting the new version of the manuscript.
Validity of the findings: The results and discussion sections are well presented and in accordance with the aims of the manuscript. However, a detailed description of the limitations of this study and future work should be included by the authors into the discussion.
Additional comments: This manuscript presents the evaluation of the energy cost of transport and EMG during walking and running conditions to study the mechanisms that occur in the transition from walking to running. However, I think the authors need to address a few queries included in the document attached to improve the quality of the manuscript.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: WHY DO WE TRANSITION FROM WALKING TO RUNNING? ENERGY COST AND LOWER LEG MUSCLE ACTIVITY BEFORE AND AFTER GAIT TRANSITION UNDER BODY WEIGHT SUPPORT
Review round: 1
Reviewer: 3

Output:
Basic reporting: Language is generally clear and proper/professional English although there are numerous small typos and some cases of poor grammar, e.g. Lines 54-55: "recent studies showed a decrease in muscle activity of the TA in association with its motor unit recruitment pattern became lower", and Line 101 I could not determine what the abbreviation ES referred to.

Literature cited was appropriate in terms of breadth and depth although I think additional citations are needed to support the hypotheses and some of the discussion and interpretation on the EMG (please see more specific comments below on the hypotheses and in Box 3 below on EMG).

Structure was appropriate.

Appropriate testable hypotheses were posed although I was unclear how they related to the research question emphasized in the Introduction of further clarifying the triggers of the gait transition.  The Introduction would benefit from greater clarity in explaining the expected results.  Formal scientific hypothesis has two parts: an expected result and an explanation why that result is expected.  The former part was clear to me but the latter was not.

For example, the Introduction focused on how some studies suggest TA is the muscle-level trigger for gait transition while others suggest it is the plantarflexors.  How is an experiment with manipulated body weight support expected to clarify this issue, e.g. is it expected that body weight support would preferentially decrease the demand on the plantarflexors, which are major contributors to body weight support in both walking and running (Neptune et al., 2004; Hamner et al., 2010), vs. the TA which is in most studies not a major contributor to support?

Relatedly, little was made of the finding that the PTS and EOTS seemed to be much closer to each other without the simulated reduced gravity.  The discussion commented on this briefly (Line 210) but this comparison was not tested statistically (I think it should be) and was not discussed extensively in relation to the muscle-level results.  I think this is an important point to discuss towards the goal of clarifying why humans change gaits.  It would also help to raise this point first in the Introduction to motivate testable hypotheses, so that the discussion then circles back to it later.
Experimental design: In the sample size justification, please justify the effect size, i.e. why is 0.30 sufficient for this research question, beyond a citation to Cohen.  It was also not clear what statistical test this effect was for.  It may be helpful to report the minimum detectable effect of this sample size in terms of the actual outcome variables (e.g. what was the minimum detectable difference in speeds, or metabolic costs?) as readers in the field will have a better sense for whether these differences are "small", "large" etc.

In most of the cited gait transition studies, comparisons were made of measurements taken at the subject's actual transition speeds, i.e. walking vs. running at 100% of the walk-run transition speed, and data are measured for walking and/or running at an overlapping range of speeds around the transition speed to determine variables like the EOTS.  Here the protocol seemed considerably different: in the first part, subjects walked at several speeds and ran at several speeds, only one of these speeds was performed at both gaits (2.0 m/s), and the EOTS appeared to have been determined by extrapolative curve-fitting since it was faster at least on average than the fastest-tested walking speed in either condition.  This was concerning because there is often considerably scatter in experimental data around the typically-assumed quadratic relationship between walking speed and metabolic rate.  This point is difficult to address without a large effort of collecting new data but at a minimum it should be discussed in terms of implications/limitations/sensitivity.

For example, concerning the quadratic relationship and fitting of the experimental data, some recent studies have suggested fairly convincingly that the metabolic rate vs. speed relationship for running is not linear and as a result the metabolic cost of running is not invariant of running speed at least in some runners (Steudel-Numbers & Wall-Scheffler, 2009; Batliner et al., 2017).  Did the authors consider also fitting a nonlinear to model to the running data and does this affect results?

In the second part of the protocol, a ramped increase in treadmill speed of 1.67 (m/s)/s was described.  Here again it was not clear if data at the actual transition speed were obtained or if the speed was steady for an appreciable period of time.  The text read as if the treadmill steadily accelerated at 1.67 m/s^2.  I think readers will need to see more details on this protocol to be clear on what was done and what data were obtained.
Validity of the findings: The interpretation of the changes in EMG data seemed overstated.  While this was not stated directly, it appeared to me that these results were interpreted as evidence of change in the type of motor units recruited, assuming the classic Size Principle holds.  If this is assumed in interpreting the data, this assumption should be stated clearly in the text with supporting references.  To my understanding, the strong evidence for the Size Principle is largely from isometric contractions and it is unclear if it holds in general for dynamic contractions like those in gait (for example see review by Hodson-Tole & Wakeling, 2009).

Similarly, concerning the EMG MPF results, it is unclear and contentious if "spectral properties" of surface EMG signals indicate motor unit characteristics and recruitment patterns (see Point-Counterpoint exchange in Journal of Applied Physiology 2008 volume between Farina and Wakeling).  Here as well, it is suggested the authors state this assumption directly with references to support it, and discuss its implications/limitations including contrary evidence.
Additional comments: No additional comments


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: WHY DO WE TRANSITION FROM WALKING TO RUNNING? ENERGY COST AND LOWER LEG MUSCLE ACTIVITY BEFORE AND AFTER GAIT TRANSITION UNDER BODY WEIGHT SUPPORT
Review round: 2
Reviewer: 1

Output:
Basic reporting: OK
Experimental design: OK
Validity of the findings: OK
Additional comments: The authors have been very responsive to my comments.
However, their added explanation of their device now prompts me to ask that the authors re-title their paper and re-name their device. I request that throughout the manuscript, they replace “simulated reduced gravity” with “body weight support, BWS”. This is not too difficult to do and I feel it is more accurate description of the device. It is a simple way to avoid appearing in contrast to previous studies of W-R transition in devices that more closely simulate RG by minimizing fluctuations in the upward applied force. The authors may also wish to change Normal Gravity (NG) to simply Normal Walking, NW. The authors should in any case use the phrase “in both conditions” rather than “in both gravity levels”. I suggest that they use the search function of their word processor and look for each instance of “gravity” and correct accordingly. The authors should also search for RGS, NG in both the text and their Figure captions and Figures.

Specific suggestions
L17 …(CoT) has been suggested as an explanation for the walk-run transition in human locomotion.
L19 triggers
L26 I still think the units for acceleration are not correct. If initial velocity was zero and a = 0.278 m/s^2, then in 60 seconds (1 minute), the velocity would be (v = at),  60 x 0.278 or 16.68 m/sec (faster than Usain Bolt). If 1km/hr per minute is correct, then the authors should state that acceleration was 0.278 m/sec/minute or calculate m/s^2 correctly.
L40 …in facilitation of economical energy expenditure.
L44 In walking, there is …
L46 … is approximately constant
L49 5-6% faster
L60 These findings suggest that
L78 plantar flexors (plural)
L126 The relationship between CoT values…
L134 only the faster one…
L143 …tape to avoid disturbing the locomotor tasks.
L146 …to visually detect when the participant…
L148 cut sentence: Note that the values…
L152 fix 0.278 again
L161 Please specify the gain. “The EMG signals were amplified with a gain of XXX (BA 1104B, Digitex….”
L165 …was applied to the stored EMG signals
L165 mean power frequency (spelling)
L166 … Wakeling, 2004). An alteration of the MPF…
L186 COT-s  (not v)
L186 under the two conditions.
L219 5-6% slower
L238 Indeed, the MG
L246 Considering muscle activity…
L284 add a sentence …the vertical force. Thus, we use the term body weight support (BWS) rather than simulated reduced gravity. In these previous studies…
L288 …yielded relatively large fluctuations of the vertical force. This intrinsic characteristic of our apparatus could reduce the mechanical power output…


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: WHY DO WE TRANSITION FROM WALKING TO RUNNING? ENERGY COST AND LOWER LEG MUSCLE ACTIVITY BEFORE AND AFTER GAIT TRANSITION UNDER BODY WEIGHT SUPPORT
Review round: 2
Reviewer: 2

Output:
Basic reporting: Authors have provided a detailed response for my suggestions.
Experimental design: No comments.
Validity of the findings: No comments.
Additional comments: No comments.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: WHY DO WE TRANSITION FROM WALKING TO RUNNING? ENERGY COST AND LOWER LEG MUSCLE ACTIVITY BEFORE AND AFTER GAIT TRANSITION UNDER BODY WEIGHT SUPPORT
Review round: 2
Reviewer: 3

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: I think there are still some major issues with the manuscript that need to be addressed through revision to the content of the paper, not just through responses to the reviewer:

- The sample size is not justified.  It should be justified using an effect size that is meaningful for this particular area of study, not an arbitrary effect size that Cohen says is large.  If there is no area-specific basis for the sample size, I think the authors should simply state that the study was exploratory in design and report the minimum detectable difference.

- I still have a major concern on the determination of the transition speed's metabolic rates by extrapolation.  The authors misunderstood my statement in the original review on scatter in the data (I assume the authors don't actually think there is no scatter in their experimental data).  The issue here is extrapolation outside the range of the measured data for either gait may inaccurately estimate an unmeasured metabolic rate, particularly at an unusual speed.  No substantive change or addition to the content of the manuscript was made in response to this concern.  Combined with the differences in equipment highlighted by Reviewer #1, it is difficult to be confidence the results (vs. other similar studies) are due to the independent variables vs. due to the protocol and equipment.  Confidence here, at least on the element of the extrapolation, could be gained if it is shown that the results are insensitive to the method of extrapolation.  The authors stated in their response that this is so but there is no evidence in the paper that this is so.

- Relatedly, the new information added on the fluctuation of the vertical force is a concern.  I was unsure if I understood the function of the device exactly, but if the amount of force applied depended on the phase of the gait cycle as stated and with the stated spring stiffness, it seems that there would be fairly large fluctuations in the force during the gait cycle, up to perhaps ~ 500 N or so in running.  Is this not a large departure from the paradigm of simulated reduced gravity, where the force would be expected to be constant?  A graph of the force-time was requested but I did not see where or if this was included in the revision.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: WHY DO WE TRANSITION FROM WALKING TO RUNNING? ENERGY COST AND LOWER LEG MUSCLE ACTIVITY BEFORE AND AFTER GAIT TRANSITION UNDER BODY WEIGHT SUPPORT
Review round: 3
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: No additional comments


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: MANAGING MIGRAINE WITH OVER-THE-COUNTER PROVISION OF TRIPTANS: THE PERSPECTIVES AND READINESS OF WESTERN AUSTRALIAN COMMUNITY PHARMACISTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: •	Clear and unambiguous, professional English used throughout.

The language is intelligible and professional. There are some parts of the manuscript which could be clearer (aim and parts of the methodology, as mentioned later in this review).

•	Literature references, sufficient field background/context provided. .

Line 77 Is there more recent information about migraine prevalence (beyond the 2007 reference)?
Lines 82-83 Perhaps you could be explicit about what is currently available OTC in Australia to manage migraines, rather than just stating that triptans are not. This might help the international readership and provide more context. For example, in addition to simple analgesia and some combined analgesia products, the UK would have buccal prochlorperazine (Buccastem M) licensed for the treatment of nausea and vomiting associated with migraine. Is that available in Australia too? Oral diclofenac was reclassified back to POM in 2015 and buclizine hydrochloride (as an anti-emetic) is limited in usefulness due to being in combination with a codeine-containing product. Metoclopramide is POM is the UK.
Line 90 You could potentially mention Cochrane Systematic Reviews, such as:
o	Derry CJ, Derry  S, Moore  RA. Sumatriptan (all routes of administration) for acute migraine attacks in adults ‐ overview of Cochrane reviews. Cochrane Database of Systematic Reviews 2014, Issue 5. Art. No.: CD009108. DOI: 10.1002/14651858.CD009108.pub2
o	Bird S, Derry  S, Moore  RA. Zolmitriptan for acute migraine attacks in adults. Cochrane Database of Systematic Reviews 2014, Issue 5. Art. No.: CD008616. DOI: 10.1002/14651858.CD008616.pub2
Starting Line 112 While sumatriptan has been available OTC in other countries/regions for several years, is there any evidence that this deregulation has been successful/beneficial? Perhaps such information should/could affect the decision by ACMS to reclassify? When I asked UK pharmacists about it around 10 years ago as part of my doctoral research, they didn’t seem to have favourable opinions on it.
Line 384 “this study is the first providing information on the perspectives and readiness of community pharmacists to manage migraine including OTC provision of triptans”. There is other work that has gleaned information on UK pharmacists’ views on OTC deregulations including sumatriptan [Hanna LA, Hughes CM. Pharmacists’ attitudes towards an evidence-based approach for over-the-counter medication. International journal of clinical pharmacy. 2012 Feb 1;34(1):63-71].
Line 437 - the Royal Pharmaceutical Society of Great Britain (RPSGB) is now known as the Royal Pharmaceutical Society (RPS), not RPSGB. A manufacturer of OTC sumatriptan (Imigran Recovery) also provided support material https://www.chemistanddruggist.co.uk/feature/imigran-recovery

•	Professional article structure, figures, tables. Raw data shared.

The suggested format of the manuscript has been followed. It is difficult to check word count in the pdf, but the abstract appears to be around 370 words.
Figures seem clear, the only minor comment is that they could include the question number (not necessarily the question part) like has been done for Table 3.
Raw data/data collection tool: The final version of the instrument (questionnaire) has been uploaded although it’s not clear whether the few sentences at the start is the ‘cover sheet’ in its entirely, or whether more information about the study was provided in the survey package and/or via the telephone call. The raw questionnaire data has been provided within a spreadsheet. This appears to align with the questions in the questionnaire (columns of the spreadsheet) and with the response rate of 114 (number of rows in the spreadsheet). It would be helpful to provide a key too which shows the questionnaire options mapped to numerical coding in the spreadsheet (e.g.
Male = 1, Female = 2, Other =3;
Strongly agree = 5 to Strongly Disagree = 1 etc.
The figures and tables do not appear to have been inappropriately manipulated - it’s difficult to say definitively as there are no frequency totals in the raw data spreadsheet or explanations about what the numerical codes mean.
Figure 2: “Respondents knowledge…” should be “Respondents’ knowledge…”
There is some repetition of results (text and tables); potentially the text could be more succinct or differ from the information presented in the table.

•	Self-contained with relevant results to hypotheses.

Abstract Method/results: Some of the results could align a bit more closely to the information provided in the Method. The Method states you were ascertaining: “their knowledge of optimal migraine treatment as per current guidelines, the resources required to appropriately recommend triptans…”  Therefore, maybe rephrase the results about the first line agents to be in the context of respondents’ knowledge of optimal treatment and consider including something about their views on what resources would be required to enable an appropriate recommendation of triptans. Abstract Discussion/results: it is difficult to see where the information in the discussion is derived from (assuming the abstract is a stand-alone piece), for example, that they were knowledgeable regarding triptans, recognised symptoms requiring referral, but that their migraine knowledge could be improved. None of these points are really apparent from the results presented.
Experimental design: •	Original primary research within Aims and Scope of the journal.

Yes

•	Research question well defined, relevant & meaningful. It is stated how research fills an identified knowledge gap.

A research question could be included in addition to the study aim/objectives. The aim could potentially be clearer. You state: “evaluate the…readiness…to manage migraine including over-the-counter (OTC) provision of triptans”. Were you measuring their readiness to manage migraine (in a general sense, which could also include triptans) or their “readiness to manage migraine with triptans” (given these aren’t OTC options currently). Perhaps an explanation or definition about “readiness” would be useful - if readiness encompasses confidence and knowledge (as mentioned on Line 149 in the context of previous work) do you need to have knowledge as a secondary objective? This applies to abstract and main manuscript.

•	Rigorous investigation performed to a high technical & ethical standard.

See below – the manuscript could include more information about what the respondents knew about the study prior to participation (in terms of consent/voluntary participation/how their data would be used/stored/whether it was anonymous or could be traced back to a specific pharmacy). Was all of this provided in the survey pack or discussed in the telephone calls? Information about ethical approval is provided within the manuscript on Lines 164-165 i.e. the study was approved by the Human Research Ethics Committee of Curtin University (HRE2018-0072).

•	Methods described with sufficient detail & information to replicate.

Line 173 After describing the development of the questionnaire, you could mention that it is provided in the appendix/available on request from the authors.
Line 181 You could also explain why hospital pharmacies were excluded from your study (is it because they don’t stock OTC medicines/wouldn’t be providing self-care advice/medicines?). You could outline various ways you tried to maximize the response rate (and hence reduce non-response bias) from the outset e.g. reminders, incentives, developing a relatively short questionnaire etc.
Line 186 Please expand on what information was provided on the participant information sheet – did it make it clear that participation in the study was voluntary, purpose of the study, estimated time for completion, how their data would be stored/used? Was consent implied or did you have something relating to this on the cover sheet so that you actually obtained written consent?
Lines 188-189 Can you explain more about the coding of the questionnaires for the purposes of targeting non-responders i.e. does this mean that responses were only partially anonymous as the questionnaire could theoretically be linked to a specific pharmacy? And if it could be linked to a specific pharmacy, were all the demographic questions necessary?
Lines 194-195 You state: “Responses received prior to 11 May 2018 were included in the study analysis.” Perhaps you could explain a bit more about this date (i.e. there was an extended deadline to that initially stated on the questionnaire in order to maximize the response rate) since the questionnaire uploaded as supplementary material states “Please kindly return the completed questionnaire in the reply-paid envelope enclosed by the 23rd of April 2018.”
Validity of the findings: •	Impact and novelty not assessed. Negative/inconclusive results accepted. Meaningful replication encouraged where rationale & benefit to literature is clearly stated.

You have presented a mixture of positive and negative findings/opinions and openly discussed these. This work is particularly relevant for Australia given that OTC sumatriptan is already deregulated in other parts of the world (including the UK and other parts of Europe and New Zealand for around 10 years). Perhaps you could mention that while this study focuses specifically on migraine and migraine medicines, the questionnaire could adapted for other clinical conditions/potential POM switches (or other suggestions for future research priorities)

•	All underlying data have been provided; they are robust, statistically sound, & controlled.

This seems fine. You could clarify whether data entry was done by one person and then accuracy checked by another independently etc. Also, was a script followed when contacting the pharmacies by phone to ensure consistency of approach.

•	Conclusions are well stated, linked to original research question & limited to supporting results.

As previously mentioned about the abstract discussion/results: it is difficult to see where the information in the discussion is derived from (assuming the abstract is a stand-alone piece), for example, that they were knowledgeable regarding triptans, recognised symptoms requiring referral, but that their migraine knowledge could be improved. None of these points are apparent from the results presented.
I think you might want to mention that readiness to supply (and adequate support to do so) could still mean that a supply cannot be made due to the manufacturer’s restrictions. For example, the electronic medicines compendium https://www.medicines.org.uk/emc/product/209/smpc outlines the numerous restrictions imposed by the manufacturer in relation to their product Imigran Recovery and it “should only be used where a clear diagnosis of migraine has been made by a doctor or a pharmacist. For pharmacy supply, patients should have an established pattern of migraine (a history of five or more migraine attacks occurring over a period of at least 1 year).” There are numerous cautions and contra-indications too.

•	Speculation is welcome, but should be identified as such.

It is clear when the authors are speculating/postulating about their findings.
Additional comments: This was an interesting piece of work and perhaps future research could ascertain opinions of reclassifications (potential and existing) given the drive for self-care and self-medication.

I have undertaken the peer review using the journal's criteria (these are bullet points throughout the review) and provided comments about each.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: MANAGING MIGRAINE WITH OVER-THE-COUNTER PROVISION OF TRIPTANS: THE PERSPECTIVES AND READINESS OF WESTERN AUSTRALIAN COMMUNITY PHARMACISTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall, this was an interesting paper with information presented logically and coherently throughout. The writing is of a very high standard with only a few typographical errors e.g. lines, 113 and 136. I would suggest that units are used throughout the text when referring to age e.g. line 299, 51 years rather than 51.

The introduction to the paper provides a detailed background to triptan deregulation with appropriate references cited. This section could be improved by providing a summary table of licenced drugs for migraine treatment available OTC or under pharmacist supervision. This would be particularly beneficial for international readers in terms of context. For example, metoclopramide is discussed later in the manuscript, but this is a prescription only medicine in the UK.

No issues with any other aspects of ‘basic reporting’
Experimental design: No comment
Validity of the findings: In general, the findings have been clearly identified and appropriately discussed. There is some restating of results within the discussion (lines 488-503).

Could have further review within the discussion on the potential impact of triptan deregulation. What can be learnt from the experience of other countries? E.g. it has been stated by Paudyal et al. 2013 that the reclassification of sumatriptan in the UK has been not been particularly successful. Another study by Hanna et al. 2016, reported that pharmacy students’ in the UK thought that the product licences were too restrictive and may be a barrier to self-care.
(Vibhu Paudyal, Denise Hansford, Scott Cunningham, Derek Stewart; Over-the-counter prescribing and pharmacists' adoption of new medicines: Diffusion of innovations, Research in Social and Administrative Pharmacy, 9:3, 2013, Pages 251-262)
(Lezley-Anne Hanna, Maurice Hall, Deirdre Duffy; Pharmacy students’ use and views on over-the-counter (OTC) medicines: a questionnaire study, Currents in Pharmacy Teaching and Learning, 8:3, 2016, Pages 289-298)

Supplemental data has been provided, but it is noted that there was an ‘additional comments’ section within the questionnaire. Were the responses obtained analysed? If so, what were the key findings. If not, why was this the case?
Additional comments: Overall, a very interesting paper with insightful and relevant findings.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: MANAGING MIGRAINE WITH OVER-THE-COUNTER PROVISION OF TRIPTANS: THE PERSPECTIVES AND READINESS OF WESTERN AUSTRALIAN COMMUNITY PHARMACISTS
Review round: 1
Reviewer: 3

Output:
Basic reporting: This is a well written manuscript with clear and unambiguous reporting. Literature used well to set the scene and the structure and figures support the authors' arguments. I particularly liked Table 1 and the mapping of domains to study objectives.

Some minor comments re. presentation (particularly for an international audience):
What is the difference between a metropolitan and a regional community pharmacy?
What is "Accredited pharmacist status"? This needs addressed early in the paper as it became a significant variable in the findings.
What is the process for Emergency supplies and is there any literature to support prevalence of their use in general in Australia?
What is the purpose of metoclopramide i.e. anti-emetic - useful for the non-expert reader?
Line 469 To the author’s knowledge - should be plural.
Experimental design: This study makes an original contribution to knowledge in this area and the study has been robustly designed and executed. Methods are clearly described.
Validity of the findings: Clear rationale for what this study adds to the literature and the limitations. Clearly stated conclusions which in the main are supported by the findings. Minor comments:

Line 385 ... of migraine by pharmacists [in this study!] conforms to Australian treatment

542  ... Professional pharmacy bodies in Australia should consider these findings when considering recommendations for further Schedule 3 medicines to become available in Australia.
In my opinion, this statement is too far reaching, given the findings. Prof bodies should consider these findings when considering down-scheduling of triptans and the study may form useful background when considering other schedule 3 medicines - I would recommend rewording this final statement.
Additional comments: Thank you for the opportunity to review this interesting and well written paper. The research is robust and adds to knowledge in this field. My comments relate mainly to presentation, in particular for an international audience.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: MANAGING MIGRAINE WITH OVER-THE-COUNTER PROVISION OF TRIPTANS: THE PERSPECTIVES AND READINESS OF WESTERN AUSTRALIAN COMMUNITY PHARMACISTS
Review round: 2
Reviewer: 1

Output:
Basic reporting: As previously stated, the language is intelligible and professional.
In this revised version:
References have been added that should be useful to the international readership.
Raw data has been shared and this makes more sense now that a key has been included. Structure is fine and figures have clearer labelling.
Results are more succinct and easier to follow, as is the case for the abstract too (aligned to aims)
Experimental design: As previously stated, this work falls within the scope of the journal.
In this revised version:
The research question is clear, relevant and meaningful and it is apparent how this study adds to the existing body of work already conducted in this area.
In terms of rigour and ethical considerations, the aim and methodology have now been amended to a satisfactory level. More information has been provided about what the participants were told prior to agreeing to participate.
Validity of the findings: As previously stated, the authors presented a mixture of positive and negative findings/opinions and openly discussed these. This work is particularly relevant for Australia given that OTC sumatriptan is already deregulated in other parts of the world (including the UK and other parts of Europe and New Zealand for around 10 years).

In this revised edition:
The authors have now included how the questionnaire could be adapted for other clinical conditions/potential POM switches.
The authors have now clarified about data entry and accuracy checking, and provided appropriate underlying data and a coding key.
The abstract is a better stand-alone piece.
The conclusion maps to the research question/study aims and objectives.
In terms of postulating/ speculating, the authors have mentioned issues around the manufacturer’s numerous restrictions for OTC sales (i.e. regardless of the pharmacist's level of readiness)..
Additional comments: Thank you for taking my feedback and suggestions on board; I think the paper has been substantially strengthened now.