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 EFFECTS OF FAMILIARITY ON ESCAPE RESPONSES IN THE TRINIDADIAN GUPPY (POECILIA RETICULATA)
Review round: 2
Reviewer: 2

Output:
Basic reporting: No further comment
Experimental design: I have no specific comments about the experimental design, which was generally ok.
Validity of the findings: I have a number of important concerns about the validity of the findings and their interpretation. First of all, it is unclear what specifically the authors analysed to compare the responsiveness between familiar and unfamiliar groups and there was no way I was able to replicate their result with the provided data and only non-significant effects were acquired.  Secondly, for the other four analyses the authors used a GLM approach and therefore forgot to account for non-independence between the groups and should therefore have used a mixed modelling approach (GLMM). This is likely to considerably change results. Thirdly, the authors refer to significant effects of familiarity while there are none, to multiple significant effects of length where there is only one, and make wrong interpretations on finding a significant effect. From the data and results quite an extent of the discussion seems not appropriate as the effects described seem to be different than interpreted.
Additional comments: Besides my main concerns about the analyses and their interpretation and the other points below, a more important general point is that the study is still lacking is a good explanation of the mechanistic expectations and interpretation of why familiarity would matter in fast startle responses, especially in the introduction. This point should be well thought about and integrated and, together with clarifications to the reasoning for doing this specific study, besides because it has not been done yet, the manuscript will be improved.

Line 24: This sentence remains ambiguous and best to remove “during early life stages “ or make clear also the experiments were conducted in the same life stage.
Lines 30-31: See points below, I do not think the result holds and that therefore there are no significant effects of familiarity on responsiveness in the specific situation tested.
Line 32-35: Not “more” as familiarity had no effect and furthermore size only had an effect on reactive distance!
Lines 60-62: Familiarity itself does not have anything to do with individuals, therefore be careful with defining it here.
Line 64: Please rephrase this sentence. Repeated exposure to a stimulus can lead to familiarisation, in a social context that may thus be conspecifics with whom an individual interacts, such as during foraging.
Line 64-67: This can give greater fitness benefits/this has been shown for a couple species but be careful with making such a general statement as it may be species or context dependent.
Line 70-71: Again, don’t generalise too easily.
Line 73-75: Same.
Line 77-83: This depends strongly on the species and the type of social system, for example much more likely in birds with strong social structures and many repeated interactions than in fish that live in very large fission-fusion populations.
Line 86-87: This sentence seems to show the opposite of what is stated in the foregoing sentence.
Line 104-107: It remains unclear why exactly familiarity would need to be investigated in the context of escape response and thus why the study was conducted. Stating that “how familiarty shapes predator evasion … remains unexplored” (Lines 85-86) and “Dominici calls for… all espects on an escape response” (lines 103-104) do not give clear reasoning why this would be needed.
Line 120-122: But why? What mechanisms are fundamental to your prediction?
Line 163-169: So was there was a difference in the way fish were placed in the observation chamber for testing as fish from familiar groups would be placed there together and fish from unfamiliar groups one at a time? This could have a number of effects and should be clarified.
Lines 163-169: Thus each group received one test trial? This needs to be clarified.
Lines 198-214: These two paragraphs need to be integrated into one, which can be half the length.
Lines 227-238: The authors need to make clear if they run analyses at the individual or group level. If at the individual level they cannot do a GLM as they have to account for non-independence within groups by running a mixed model and group id as a random factor. Furthermore, the way how responsiveness is analysed is not correct (see below). Also, if the analyses were run at the group level it needs to be clarified how body length was calculated per group.
Lines 244-246: Statistically testing this, such as with a Chi-squared test, shows there is no significant difference between the groups in any fish responding or not. This should be integrated here.
Lines 246-248: I don’t understand what the authors analysed here and I cannot replicate their result. It seems the authors want to compare the average nr of responsive individuals per group between the treatment. But running this actual analysis with a Wilcoxson rank sum test yield a non-signifant result. Running this with all groups with zero responders excluded still results in a non-significant result so it is mysterious what the authors actually did. Also, here it can be clarified that for double the number of groups in the unfamiliar groups no individual responded compared to the familiar groups, although that effect was als non-significant.
Line 253-258: This section is confusing and seems to make false interpretations. From Table 1 it is clear that neither treatment or length had a significant effect on the reactive distance nor was there an interaction between them. This needs to be stated first of all. Secondly, that the intercept was significant simply means that it for all individuals on average it was significantly different from zero, which is not that informative for your questions. Thirdly, as you don’t find an interaction to be significant there is no difference in slopes, which is now argued on line 255.
Line 263-265: Length was only significant for maximum speed, thus again, this statement is false.
Line 266-271: The table clearly shows there was no significant interaction between familiarity and body length thus does not support this statement and interpretation!
Results: From the model output in Table 1 the (lack of significant) results are clear to me: familiarity and body length did not interact and did not have an effect on the reactive distance, maximum speed, maximum acceleration or total distance. The only significant effect observed was unsurprisingly that larger fish reached a higher maximum speed.
Line 278-279: The authors actually do not show this as their only significant result for familiarity cannot be replicated. Furthermore, as the previous reviewers also already highlighted the authors should not make too strong statements and try to oversell their results.
Line 280-281: This is purely hypothetical and has no place in the first paragraph of the discussion.
Line 283-284: Again the authors make a statement about an apparent significant result that is not signifant (at least to table 1)!
Line 285-286: Even if this effect would be significant it does not really say anything about how groups respond but how individuals in such a group respond.
Line 287: See other points, the result on which this statement is based needs to be clarified/rectified and may considerably change the discussion.
Line 287-316: A likely alternative explanation is that fish in familiar groups are more at ease as they are with individuals they have seen before.
Line 342-343: Some more sentences about the relevance of studying such a fast and innate response as studied here would be helpful as it may explain the lack of significant results.
Line 354-355: I wouldn’t call one significant effect far greater
Line 361: The test used was not novel altought the sentence currently seems to suggest that.
Line 363-366: Please see other comments about the underlying analysis and be careful about statements about behaviour being ‘adaptive’ as finding significant relationships between behaviours does not require any adativeness.
Comment 7 Reviewer 2: This reviewer makes a fair point that I don’t think the authors address satisfactory. The authors should at least make the suggestion by the reviewer clearer in their discussion. With the current analyses the authors did (i.e. not controlling for group) it is hard to know for certain if it was indeed not always individuals of a certain size responding quicker.


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 EFFECTS OF FAMILIARITY ON ESCAPE RESPONSES IN THE TRINIDADIAN GUPPY (POECILIA RETICULATA)
Review round: 3
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Comments on Wolcott, Barbosa and Ojanguren 9-11-17
I have studied the responses to Reviewer 1 & 2, and generally I’m satisfied that you have adequately addressed their concerns, as well as my own (#3). I believe that statistical analysis is much improved over the original, and I agree with the  decision not to use an analysis of residuals.
I think you have gotten an interesting result in the finding that familiarity does not affect all components of the escape response. The findings relative to size effects are also noteworthy. I think these will be useful to those working in this field. One of my thoughts on the results is that individuals in groups of familiar individuals ‘feel safer’ and hence react less to stimuli than those among unfamiliar individuals. I might avoid saying that they feel more at ease, which, unlike ‘feel safer’, is not standard in the behavioral literature, as far as know.
Below. I have made more suggestions. Most are of an editorial nature. I think the abstract was generally overlooked in the original reviews, because it seems to need a bit more work.
24 I would take out “antipredator”. All you need for clarity is “escape responses”
24 Suggest “the guppy, Poecilia reticulata”. Drop “Trinidadian”
30 ‘surprisingly’ = ‘contrary to the prediction’
30 ‘by’ instead of ‘of’ ?
31-32 Take out the plausible sentence, as this opinion is better left for the discussion
33 insert ‘rather’ after ‘size’
35-36. I think you should revise this. Rather than advocating for your ‘approach’, which is not the subject of this study, try a sentence that summarizes or gives your most salient conclusion. How about the last sentence of the Discussion? Something that grabs the reader’s attention.
64 insert ‘and’ after the comma
65 ‘thus’ take out
109-112 Somehow, I think this sentence is out of place.  It doesn’t logically lead to 112, as yours is not an integrated approach, right?
113 ‘shaping’ = ‘affecting’
115-116 Here’s a suggested rewording. Guppies shoal . . . . birth. During this early developmental period, guppies acquire group familiarity and its associated antipredator benefits (  ). Does such familiarity then lead to greater group cohesion, e.g. as in avoid joining a different group?
However, the whole paragraph seems not to hang together very well. The points are not flowing logically to me. Suggest revisiting it. I think you need to better set the stage for you important last paragraph, the statement of purpose.
120 doesn’t flow logically from 119.
170 ‘by’ instead of ‘of’
172-175. Here’s another suggestion for wording. ‘Familiar groups consisted of individuals that were together for two weeks. Unfamiliar groups were comprised of individuals taken singly from different holding tanks.’
You can omit the rest, i.e. …not seen each other before and put them together…
232 typo, check ‘…both response variables,
231-234 The ANOVA model assumes normality and homogeneity of variances of residuals, and also independence of residuals when you analyze responses on the dependent variable. I think you might simply say that normality and homogeneity assumptions about the distributions of residual values on the dependent variable were improved by log-transforming the response variables. The analysis is generally robust to small deviations, and it is usually pretty hard to absolutely meet all the assumptions. I think your results are clear enough. That’s my opinion.
239 Try ‘Individual S.L. did not differ…
240 (SD)
278 ‘quality’. This word seems a little vague to me. Not sure exactly what it means. You might say ‘… some aspects of the escape response’ or something to that effect.
298. Why not ‘feel safer’ rather than ‘at ease’?
367 Again, maybe ‘quality’ should be ‘specific components of’

I trust that you will find these comments useful overall.
Doug Fraser


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: EVIDENCE FOR CONTINUAL HYBRIDIZATION RATHER THAN HYBRID SPECIATION BETWEEN LIGULARIA DUCIFORMIS AND L. PARADOXA (ASTERACEAE)
Review round: 1
Reviewer: 1

Output:
Basic reporting: The grammar needs attention (e.g., the first sentence is a sentence fragment, and the word “still” makes the title of the paper confusing—it suggests that something about the nature of Ligularia x maon… has changed). In some places the grammatical problems make this manuscript difficult to follow, and thus difficult to review. Some of the ideas present may benefit from clarification/substantiation, but that’s hard to assess currently.

Considering hybridization “one of the drivers of speciation” is a little bit strong for the first sentence of the paper—that’s a somewhat controversial/complex claim.

Ln78 – provide citation for these species belonging to this section. And introduce the family affinities of this genus at some point?

The introduction might be more effective if it were more tightly organized/clarified. E.g., a section on the evolutionary significance of hybridization, followed by a section on Ligularia, followed by a section on the specific study system, and its relation to the hybridization question.

Ln94 – it’s unclear at this point what the distinction is between “natural hybrid species” and “hybrid offspring.”

The voucher information in table S1 is incomplete. Each studied population should be supported by at least one voucher, deposited in an official herbarium (collector number and herbarium of deposition need to both be indicated here).

The beginning of the Discussion belongs in the Introduction.

Fig. 1 – it would be more informative to present a most-parsimonious tree (rather than a consensus tree) and to then label the branches of that tree with the bootstrap support values. Strict consensus trees don’t have very much information in them.

Fig. 2 – Interesting (odd?) that relatively few of the hybrid sequences are the same as the most-common haplotype from either parent. Instead, many of the hybrid sequences are unique. Is this an artifact of the fact that the sequences from the hybrids were cloned (and thus have more PCR errors, etc., in them), and the parental accessions were direct-sequenced?

Fig. 3 – Something is wrong with this tree. Is it also a consensus tree? Instead, a single most-parsimonious tree should be presented, with meaningful branchlengths, and bootstrap support values added on.

Fig. 5 – This figure would be clearer if each of the parental species got the same color in each of the panels.

A figure showing some plants of each taxon would be a welcome addition to the paper.
Experimental design: It’s not clear (at least not in the beginning) how the cloned data were used. How many colonies were sequenced? For individuals with two “alleles”, how were they analyzed?

ln141 – 1000 replicates for the best tree search? (Rather than for bootstrapping).
Validity of the findings: 224 – “almost all individuals” of the hybrid shared haplotypes with one of the putative parents. But not all? What does that imply?
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: EVIDENCE FOR CONTINUAL HYBRIDIZATION RATHER THAN HYBRID SPECIATION BETWEEN LIGULARIA DUCIFORMIS AND L. PARADOXA (ASTERACEAE)
Review round: 1
Reviewer: 2

Output:
Basic reporting: The English language should be improved to ensure that your international audience can clearly understand your text. I suggest that you have a native English speaking colleague review your manuscript. Some examples where the language could be improved include lines 62-65, 75-75 among others – the current phrasing makes comprehension difficult.
Line 103 needs more precision in concepts. “Classification” is part of a different taxonomic task. It should say: “identified” or “determined”.
Some grammar errors like spaces, periods, etc. are marked in the text.
The rest of the information about literature, figures, data, etc. have no problem.
Experimental design: Minor comments and suggestions: The plant materials acquisition must be more explicit. (lines 98-102, and 179). Say how did the authors got the F1, and F2 materials. Do specimens on F1 and F2, and from backrosses presented morphological variation?

I suggest to include the percentage of the species individuals, instead of the word "most" (line 124).
Validity of the findings: The authors are not correctly interpreting the phylograms. The explanation or interpretation in lines 228-230 of the Fig. 1 are not correct. What the authors consider as "cluster A", it is an unresolved clade formed by three different groups, and a polytomy with 22 unresolved individuals. The nrITS outcome and the provided interpretations based on the tree are erroneous.
On the other side, the description of Fig. 3 in lines 253-257 is also incorrect. The tree does not show independent clusters for L. spicata (outgroup), L. lamarum, and L. paradoxa x maoniushanensis. Even more, what they consider a clade for L. lamarum (H3 and H6) it is part of the unresolved area of the tree. You cannot consider that H3 and H6 show a closer relationship than the rest of individuals sampled.
The evidence and discussion for nrITS and cpDNA evidence for the Ligularia species hybridization and introgression patterns and processes must be reinterpreted (Some information about this can be found easyli in http://evolution.berkeley.edu/evolibrary/article/phylogenetics_03,
in http://tolweb.org/tree/home.pages/treeinterpret.html, or in Lanford, M., et al. 2014. Bioinformatics 30 (17): i519-i526. DOI:
https://doi.org/10.1093/bioinformatics/btu463

The rest of the evidence seems to support their concluisons.
Additional comments: Tha manuscript present a very interesting study to understand plant hybridization with molecular markers and analysis in an evolutionary context. However part of the phylogenetic interpretations are not correct. If they are willing to reinterpret the nrITS and cpDNA phylograms, the results, discussion and conclusions will be substantially improved.


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: EVIDENCE FOR CONTINUAL HYBRIDIZATION RATHER THAN HYBRID SPECIATION BETWEEN LIGULARIA DUCIFORMIS AND L. PARADOXA (ASTERACEAE)
Review round: 2
Reviewer: 1

Output:
Basic reporting: Grammar and English usage need further attention. References, figures, data sharing, results/hypotheses -- all seem fine (I suggest removing at least one figure -- see more detailed comments below).
Experimental design: yes
Validity of the findings: yes
Additional comments: This paper is greatly improved over the earlier version, but the grammar still needs considerable attention (at least in my opinion – ultimately this would be up to the journal). For example, in the abstract, it should be “is a hybrid” instead of “is hybrids” in the results section, and it’s unclear what “sufficient for hybrid generation determination” means. In some areas of the paper the language issues are sufficient to make it very difficult to understand what is being said.

ln69	I still feel this section is too strong, even with the stated caveat that “not all hybrids form new species.” At the least, I’d suggest replacing “they will” with “they may” on this line

88 	What is “family affinity”?

89	“affinities of many species at some point” is exceedingly vague

98	I don’t understand: “An interesting phenomenon in both populations is that some individuals are different from other, and they are typical individuals of the species.”

113	State this last point more clearly; something like: “Is L. xmao a cohesive hybrid species, reproductively isolated from its progenitors, or do the L. xmao individuals instead constitute a recurrently-formed hybrid swarm”

152	The number of clones sequenced for each accession should be included in a table if they haven’t been already.

159	You mean that a consensus sequence was used for closely-related sequences from a single individual? What cut-off was used to decide if sequences were closely enough related to merge?

163	All ITS cloned sequences were used? But then it says later that two sequences were selected. That selection process sounds suspicious – if the authors are deliberately selecting sequences that are close to the parental sequences and throwing out the rest, aren’t they biases the analyses towards the desired result?

265	Inclusion of identical sequences should not reduce resolution or support.

353	I’m not familiar with the introgression program but very small p-values typically indicate highly significant results, which I would have thought in this case would mean strong indication of introgression. That’s not the case?

383	The beginning of the discussion has already been covered in the introduction. The entire first section (“Conditions of…”) could be omitted.

469	Was the germination trail (1000 seeds) part of this study, or the earlier cited one?

475 etc	But this mechanism – that largely infertile F1s are formed at high enough rates that a lucky few produce enough seed to allow hybrids to perpetuate – is inconsistent with your data, which shows almost no F1s but a lot of F2s.

508	This section on Pinus etc belongs in the introduction rather than in the discussion

Fig. 1	Nice!

Fig. 2	This figure is still strange. Why are all the terminal branches exactly the same length? Contrary to the caption, I very much doubt that this is a most-parsimonious tree. (At least, not a phylogram, with the associated scale bar [10 changes]). A single most-parsimonious tree should be presented, as a phylogram. For individuals that had multiple sequence types present, some method should be used to show which sequences come from which accession (e.g., a series of lines connecting sequences from a given individual).

Fig. 3	I don’t think this figure adds anything to what is already shown in Fig. 2. It is not a depiction of “reticulate history” unless I misunderstand. Instead it is a haplotype network, where reticulations indicate other possible mutation paths.

Fig. 6	Strange and interesting that there’s very little evidence of F1 plants in this sample (whereas F2s seem much more common). I don’t remember that message being made very clearly in the manuscript, but I might have missed it.

Fig. 7 	I don’t know enough about this approach to be able to follow this figure. What are fAmAm and fAmAd?

Table 3		I think this table could safely be omitted.


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: EVIDENCE FOR CONTINUAL HYBRIDIZATION RATHER THAN HYBRID SPECIATION BETWEEN LIGULARIA DUCIFORMIS AND L. PARADOXA (ASTERACEAE)
Review round: 2
Reviewer: 2

Output:
Basic reporting: Just typographic errors:
Line 43: say ecidence; must say evidence
Line 235: say maoniushan- ensis; must say maoniushanensis
Experimental design: no comments
Validity of the findings: Lines 227-230, and 235-141:
The tree presented in the Fig 1 is not resolved. When a phylogeny has no resolution, you cannot describe group relationships. In this case, it is not true that the outcome resolved two phylogenetic sections (A and B, even if they resulted in the network at Fig 2, which is not a phylogeny). Hence, what the authors call section B, has the same probability to be phylogenetically related with accession H2, or with the H5-H7 branch or with any other. The order of the branches resulting from the analysis does not gives hierarchical groupings or relationship evidence. If the clade branch is not resolved at the base, you cannot say that you have a monophyletic group. There are not sections to be separated, you can say that most of the times, some samples resulted together forming branches (indicate bootstrap numbers or parsimony branches support), but that you do not know the relationships among them. I cannot agree with the tree description, interpretation, and conclusions presented.
Additional comments: Most of the evidence presented in the paper support the proposal of hybridization and introgression within Ligularia duciformis and L. paradoxa. Then I suggest to leave the phylogenetic analysis out of the paper since is not a good evidence to support the hypothesis presented in this study.


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: EVIDENCE FOR CONTINUAL HYBRIDIZATION RATHER THAN HYBRID SPECIATION BETWEEN LIGULARIA DUCIFORMIS AND L. PARADOXA (ASTERACEAE)
Review round: 3
Reviewer: 1

Output:
Basic reporting: I realize that this isn't particularly helpful, but the English grammar, etc., is still not at a state that I would be comfortable with, were I a journal editor. Perhaps peerJ can do some copy editing?
Experimental design: no comment
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: EVIDENCE FOR CONTINUAL HYBRIDIZATION RATHER THAN HYBRID SPECIATION BETWEEN LIGULARIA DUCIFORMIS AND L. PARADOXA (ASTERACEAE)
Review round: 3
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: The problems I found are solved. I think that the paper migth be published as the last version is.
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: ILLEGAL USE OF NATURAL RESOURCES IN FEDERAL PROTECTED AREAS OF THE BRAZILIAN AMAZON
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: I find the overall findings valid, however I believe it would be interesting to add in the analysis the temporal trend of the illegal use of natural resources and if this changes over time i.e. if there is an increase or decrease. Moreover, I wonder if the authors have looked at the correlation between the illegal use of natural resources and law enforcement activity (number of guards, monthly patrol etc) . Beside the PA protection category, does the presence of law enforcement activity have an impact on the number of illegal activities over time? PA protection category is not always correlated with law enforcement effectiveness.

These additional analyses would help to understand why there so many illegal activities and if law enforcement and/or the park management is efficient and effective. The take-home message would be beneficial for both managers and decision-makers. Moreover, I have an analytical concern about including both terrestrial and coastal/marine reserves – I expect that fishing activity is more present in coastal/marine areas and hunting activity more present in terrestrial areas. It would be good if this could be explored and included in the analysis.

There are many repetitions in the discussion section about the description of the results (the result section already includes it). This needs to be better structured. Moreover, I would suggest to add more literature about protection measures against illegal use of natural resources.
Additional comments: This manuscript was nicely written and interesting to biodiversity conservation and protected areas management.  I have highlighted a few areas that could benefit from some clarification or rewording, which are listed below:

L123.  IBGE, could you give the whole word Instituto Brasiliero de Geografia e Estatistica
L131. Established is repeated twice
L140-141. Can the authors add the total area (in square km) of the PAs studies overall the ones that are managed by the federal government?
L142. Can the authors add somewhere the percentage of grassland and savanna per park? Would be good a table with the PAs and the % of habitat cover types
L145 Brazilian System of Conservation Units
L146-148. Information not necessary
L181. 1 Km2 instead of from 1km by 1 km
L181. 200 m2 instead of up to 200m by 200m
L207. Please add table with results from correlations
L215. Would be nice have subtitles like in the methodology section
L271. Threatens
L294. Reference missing
L314…in order to achieve just an effective conservation, it is necessary to involve local…

Table S2. Please add a clear description of each category of illegal activity


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: ILLEGAL USE OF NATURAL RESOURCES IN FEDERAL PROTECTED AREAS OF THE BRAZILIAN AMAZON
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript’s content is relevant given the lack of studies that contemplate the illegal use of natural resources in the PAs. This kind of research is important to understand the PA's needs and to enable some strategic actions.

The MS was very well written, and brought a lot of good and recent references.
Experimental design: Some of the reviewer suggestions to improve the MS are bellow :

Line 43: Change "significant reduction in deforestation in the region" to "significant deforestation reduction in the region"

Line 117: Put the Datum used to compose the maps.

Line 126: Change "of the territory of the country" to "of the country's territory"

Line 131: Take away one the words "established"

To all figures: Put the Datum and Projection in the maps, with this anyone that reads your maps will know this information.

Figure 1:
In the legend: put the units of the “Illegal activities”, like: “Numbers of illegal activities”
Divide the legend in two columns, the map’s layout will be improved.
Suggestion to the legend order an items:

First column:
Numbers of Illegal activities
1-23
24-55
56-97
98-199
200-316

Second column:
Brazilian Amazon
Rivers
         Protected Areas
Sustainable use
Strictly protected

To all tables:Change “Brazilian reais” to “Brazilian real”
Validity of the findings: The results show the importance of your work, however i missed some explanation in the  conclusions, that how the government authorities would use this data to improve the
threats to the biodiversity in the PAs.
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: COMPLETE MITOCHONDRIAL GENOME SEQUENCES OF THE NORTHERN SPOTTED OWL (STRIX OCCIDENTALIS CAURINA) AND THE BARRED OWL (STRIX VARIA; AVES: STRIGIFORMES: STRIGIDAE) CONFIRM THE PRESENCE OF A DUPLICATED CONTROL REGION
Review round: 1
Reviewer: 1

Output:
Basic reporting: gel picture really needed?
Experimental design: some details could be in an appendix
Validity of the findings: no comment
Additional comments: when repeatly mentioning a software product or mito-genome, no need to cite again
numbers in tables should be right-justified
line 101: able to explore


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: COMPLETE MITOCHONDRIAL GENOME SEQUENCES OF THE NORTHERN SPOTTED OWL (STRIX OCCIDENTALIS CAURINA) AND THE BARRED OWL (STRIX VARIA; AVES: STRIGIFORMES: STRIGIDAE) CONFIRM THE PRESENCE OF A DUPLICATED CONTROL REGION
Review round: 1
Reviewer: 2

Output:
Basic reporting: In general, I found the manuscript to be well written; even some of the denser parts of the Methods section were clearly worded and easy to follow.  The figures are of high quality, but some could be cut (or combined, or moved to Supplementary Materials) without significantly impacting the manuscript; see detailed comments below.  Raw sequences have been deposited in NCBI’s Sequence Read Archive, but I was unable to find Genbank accession numbers in the text for the two new sequences produced for Strix o. caurina and Strix varia; these should be provided.
Experimental design: The research described in this manuscript is original and adds to the growing body of work on avian control region evolution. Extensive detail is provided in the main text on the methods used, with further details given in the Supplementary Materials. If anything, the Methods text could be trimmed, moving more of the nitty-gritty to Supplementary Materials.
Validity of the findings: Overall, the authors make good use of their data to address questions outlined in the Introduction.  Employment of both next-gen and Sanger sequencing techniques was critical to obtaining accurate mt genome sequences for these owls.  In fact, the authors could further emphasize the fact that their study represents a cautionary case in which a next-gen-based assembly resulted in an incorrect mt genome sequence.  Given the prevalence of next-gen sequencing, combined with the fact that control region duplications have been found in a growing number of disparate avian taxa, it is important to consider the possibility of control region duplications whenever sequencing avian mt genomes.
Additional comments: I would suggest re-thinking the sub-headings used within the Methods section.  Since you have separate descriptions regarding the sequencing/assembly of the two species’ genomes, it would be nice if each description were labeled as such, and the two descriptions were structured (divided) into consistent sub-sections.

My detailed comments are listed below by line number.
l.36     At the end of the abstract, you might want to add a sentence regarding the shortcomings of short-read sequencing/assembly methods in cases like yours.
l.42     “which led to”
l.43     “of the chicken is representative”
l.100     Technically, you can’t cite (Hanna et al. 2017) in this way, since it is not published.  More correct: (Hanna et al. unpublished) or (Hanna et al. in prep.)
l.160     “amplify a slightly longer”
l.184     Did the length of the longer PCR product jive with the (incorrect) Illumina-based assembly?
l.209-214     The purpose of this comparison was not clear to me.
l.227-256     This section could be moved, so that it is presented after the description of the S.varia assembly.
l.227-228     The alligator sequence comparison isn’t mentioned/discussed later on in the text, so it’s not clear why it’s included here.  The alligator sequence is included in Figure 6, but as noted in the figure comment below, it could be cut without detracting from the conclusions.
l.238-240     See previous comment.
l.247-248     See above.
l.256     “Nuclear pseudogenation” might be a better term here, since you are referring to pseudogenes that appear in the nuclear genome.  There are also pseudogenes of mt genes that appear within rearranged mt genomes (e.g., see Eberhard & Wright 2016).
l.258     See previous comment.
Related comment: Is there any evidence of mitochondrial pseudogenes, such as those found in some parrots (see Eberhard & Wright 2016)?  There seems to be a short stretch of sequence on the 5’ side of CR1, before the hairpin sequence; any chance that it’s similar to tRNA-Glu or ND6?
l.287-292     It might be better to present the primary sequence source first, and then describe the secondary one.
l.299     It would be helpful to briefly explain that the two contigs are.
l.421     Is it possible to discount the hypothesis that the long fragment was a numt?  (or, to really play devil’s advocate, is it possible to determine that one or both of the fragments are indeed mitochondrial?)
l.446-447     This is interesting (though I don’t have any idea why this might be)!
l.453     As someone who works with other (non-owl) birds, I found these divergences to be quite high for taxa that can hybridize.  Are these levels of divergence typical for owls?
l.461-462     Identical or nearly identical CRs (e.g., as observed in snakes, e.g., Kumazawa et al. 1996, MBE 13:1242-1254) could also cause assembly problems.
l.466     “complete and accurate assembly”
l.469     “inferred the presence”
l.471     “but rather deduced that a duplication was present from the appearance”
l.475     “The mitochondrial genomes…”
l.502     “as found in some other avian taxa”
l.508     Not just Amazona parrots; also found in several other parrot taxa with independently evolved CR duplications (see Eberhard & Wright 2016)
l.517     “a proper phylogenetic test of this hypothesis, with increased taxon sampling, is warranted”
Table 1     At least one of the primers listed in the table was designed by other researchers (e.g., N1, Barrowclough et al. 1999), and this should be noted.  It would be good to add a column for references, or add footnotes, to cite sources for primer sequences, and also note which were designed by the authors.
Table 2     Some of the information presented in the table (e.g., Alignment score, Entropy) are not discussed in the text, and don’t seem crucial to the results/discussion.
Table 3     Per earlier comment (l.256), “Nuclear pseudogenes (Numts)…”  Two of the columns, E-value and Bit score, provide information that is never discussed in the text, so could be eliminated.  If they are not cut, then Bit score needs to be defined in the caption.
Figures 1&2     Both of these are beautifully drawn, but are largely redundant; could be replaced with a single figure that shows gene order surrounding the CRs.
Figures 3&4     The figure caption should also state that the locations of the goose hairpin and primer binding sites are shown.  To streamline the figure a bit, the yellow boxes labeled “control region 1” and “control region 2” could be cut, since the regions are already labeled on the left.
Figure 5     The description given in the text is probably enough, so it’s not necessary to include this figure.  If desired, it could be moved to Supplementary Information.
Figure 6     The caption refers to panels B & C, but no such labels appear in the figure.  Although the information presented in the figure is not incorrect, it illustrates only a subset of the gene orders that have been thus far documented for birds; the purpose of illustrating the owl gene order within an incomplete context is not clear.  I would recommend a figure that illustrates the gene order around the owl CRs (as suggested in lieu of Figs. 1&2), and then cite (and discuss, if you wish) other papers that have provided more complete discussion of mt gene order rearrangements in birds (e.g., Mindell et al. 1998, and more recently, Gibb et al. 2007 and Eberhard & Wright 2016).


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: INFECTION OF ARMY ANT PUPAE BY TWO NEW PARASITOID MITES (MESOSTIGMATA: UROPODINA)
Review round: 1
Reviewer: 1

Output:
Basic reporting: The writing was clear and easy to understand. The introduction provided adequate background information. There are some minor grammatical errors here and there that should be tended to.
Experimental design: •	Line 98: If the pupae were collected from Aug 2008 to April 2011, then that spans far more than just 10 months. If the samples were collected from 10 specific months, please specific which months.
•	Line 130: “Global parasitism rate” is too broad. I’d suggest the phrase “overall parasitism rate among Macrodinychus spp.”
•	Line 132-133: It’s not clear why results on number of workers are assessed. There is not reporting on this data in the results section in terms of prevalence of infection.
•	Given that the pupae were collected over a long span of time, perhaps one should look for potential seasonal or temporal patterns in infection rate.
•	Line 441: Were the differences in prevalence of infection between colonies statistically different from one another?
•	The behavior “antennated” is very similar to “ignored” except perhaps for the duration of antennation. Is this minor difference biologically relevant?
•	Some of the methods require minor clarification. For instance, the experimental could have recorded the duration of the ant-mite interactions. Would this additional data not have been useful?
Validity of the findings: •	I cannot comment specifically on the species descriptions, as this is not my area of expertise. I can comment only on the behavioral assays.
•	Line 438-441: It’s not clear what value these set of numbers provide. The infection rate of 1.69% is already reported in line 434. What is the relevance of reporting number of workers?
•	Lines 454-459: The reported values for AI are presumably in percentages, in which case the values seem exceedingly low to be biologically relevant. Can you please clarify?
•	Line 452-453: Given that there are overall differences between the different myrmecophile species, it would be useful to present a post-hoc analyses to determine which groups are different from one another (as suggested in the methods).
•	Line 474 and 488: Is there direct evidence that the mite is feeding on the hosts? The presence of a cavity does not necessarily indicate feeding. Even if the mites left behind a scar, this may be a response to the chelicerae pinching the host tissue, and not necessarily feeding by the mite. Still, please specify in the results section if scars were indeed observed in your study.
•	Lines 483-484:  This study does not actually provide experimental evidence that M. hilpertae and M. derbyensis feed on host hemolymph. This assumption is based on circumstantial evidence based on the presence of a cavity and scar, which could be a melanization response to the pinching/tearing of the chelicerae.
•	Lines 490-509: The authors suggest that the overall low infection rate may be due to that fact that the association is native. But they failed to considered a number of other alternative explanations, e.g. seasonality, spatial (nest) heterogeneity, etc. The low infection rates may also be an artifact of sampling bias. Given that pupae were collected during colony migration, and that migration may serve as a form of counter-defense, then the pupae being transported may be biased towards uninfected pupae (assuming ants can detect the difference and leave behind the infected pupae).
•	Figure 5A: The behavior “attack” is not included, is this an oversight?
•	Figure 5B: Please indicate the units for the dependent variable.
Additional comments: •	Abstract: The statement that “Our results support the hypothesis that the primary habitat of all Macrodinychus mites is the ant nest” is a somewhat of an overstatement and not really testable since one cannot conclude with full certainty that “all” Macrodinychus spp. inhabit nests. This statement is also inconsistent with lines 76-77, which state that only 1/3 of Macrodinychus species are associated with ants.
•	Lines: 511-512: This statement seems out of place as there is not further reference to the down-regulation of parasitism rates and it’s relevance to the results.
•	Lines 524-527: The rationale behind this statement is not clear. Please expand.
•	Discussion: It would be useful if the authors could discuss the potential ecological and perhaps biocontrol ramifications of this very interesting form of symbiosis.
•	Overall, the discovery and morphological description for the two new mite species is valuable. However, the results on rates of infection need to be more detailed and interpretation of the behavioral assays needs to be treated with more rigour; for instance, the discussion does not address the different behavioral responses of the ants. For instance, the discussion does not provide much context for the results reported in Figures 5A and 5B.


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: INFECTION OF ARMY ANT PUPAE BY TWO NEW PARASITOID MITES (MESOSTIGMATA: UROPODINA)
Review round: 1
Reviewer: 2

Output:
Basic reporting: AS a reviewer I am making no claim for expertise in mite systematics, but enjoy a solid description of natural history and a fascination with the communities in less known places, and that is what the present manuscript contributes along with a description of two new mite species. The dense populations of eusocial insects provide unusual opportunities for parasites and certainly the conditions where previously undescribed forms may be found. Thus, I believe this paper has clear value and perhaps a dual audience of the few mite specialists out there combined with the more abundant students of ants.

I also found the paper generally well written, especially the introduction and methods (for which I have basically nothing to say). they are were very clear to someone tangential to the topic, but I think some organizational shifts in the results and discussion will make the content more accessible for those more interested in the parasitoid system than the necessarily very complex and detailed description of mite anatomy associated with species identification.

Overall, I think the changes I suggest should be straightforward. The main point is to be consistent in the order of presentation across sections. You open with life history and focus the discussion on life history (actually you forget to discuss the new species aspects there, largely because I think you used a results and discussion approach for describing M. hilpertae and M. derbyensis, but bury the behavior in the results below the species description.  Easily fixed, I think.

1)	Start the results with the Life History and nest observations (442-467) and follow them with your description of the two species, and end results with those descriptions
2)	The genus description is not your result nor really is a key. Why not move this to the discussion as a section on Generic variation and keys to the species (my one area where I think rewriting beyond moving text is required) as you preface your key with the material at 187-217 prior to presenting 397-431.
3)	Still keep 469-527 as the start of discussion, and the Conclusion stays at the end, below the key.
Smaller points: in the systematic note (194-198), you need to translate the German group terms first and then simply indicate for precision the term used by Hirchmann, or omit that presentation if this “Gangsystematik” simply hasn’t influenced the modern systematics of the group.
At 210, to what the “Diagnosis” applies is needed. I assume Macrodinychus, but in contrast to what other genera?
249-251: adjective first…. Female or male operculum, not operculum female.
270-281, you claim you make an estimate, but report a very precise number, and similarly at  452-467, make sure significant digits are relevant to the means reported, for example 23.60 +/- 10.46 really is just 24 +/- 10, but check throughout your paper for both issues that reoccur.
360: avoid relative terms, “Legs relatively short”, in a species description lacks information without a clear contrast.
376 where you say “2, rather than 3”; to what does the 3 refer?
Experimental design: The design came out of a chance discovery, and that's ok.
Validity of the findings: solid. Aren't new species by definition "novel."
Additional comments: Figures: Hey, just nice photos.  When I read two mite species, one thinks really… you can be sure when your behavioral work often lumped the two together, and yet your photos show clearly two different animals, and they fall out separately in the key completing that story.

Perhaps most of my comments are all up in the basic reporting section, but that is the most relevant. Shouldn't take more than an afternoons work to make improvements to readability. The paper tells a good story, adds alpha taxonomy on an understudied group, and links the species to a well known host species.


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: INFECTION OF ARMY ANT PUPAE BY TWO NEW PARASITOID MITES (MESOSTIGMATA: UROPODINA)
Review round: 1
Reviewer: 3

Output:
Basic reporting: This is a nice and good written manuscript with some deficiency.
Experimental design: Acceptable.
Validity of the findings: The manuscript contains original and new spientific results.
Additional comments: This is a well-written and clear manuscript, with nice pictures and some nice drawings. The found species seems to be new, but the illustrations are not enough for a taxonomic paper. The digital pictures are nice, but not show exactly the small details of the investigated specimens. Need to add more drawings to the manuscript, the most important part of the description of the new species is the exact and clear illustration which can help the identification and recognisation of the species.

Kontschan in press paper is already published.


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: CLINICAL OUTCOMES OF RESIDUAL OR RECURRENT NASOPHARYNGEAL CARCINOMA TREATED WITH ENDOSCOPIC NASOPHARYNGECTOMY PLUS CHEMORADIOTHERAPY OR WITH CHEMORADIOTHERAPY ALONE: A RETROSPECTIVE STUDY
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1)	The article should be reviewed by a native English speaker – there are significant grammatical errors.
Experimental design: 1)	Their inclusion criteria did not require a biopsy confirmation that the residual/recurrent mass was actually tumor.  This seems a major limitation of the analysis.  They also do not describe how many patients in the surgical group had false positive resections.
2)	In the results section it is unclear whether the stage described refers to the original stage (as per standard practice) or the stage at recurrence.  Based on Figure 2, it seems they are referring to recurrent Tstage.  As a practice, these are referred to with Arabic numerals (1,2,3,4) , not roman numbers (I,II, III,IV).
Validity of the findings: 3)	The subgroup analysis involved very few patients – I am not sure how much we can rely on the validity of the data at that level.  A comment should be made to indicate these findings should be viewed as exploratory.  For instance, looking at the OS and DFS curves in Figure 5, the only group that reaches significance is surgery vs CRT for advanced disease.

4)	The inclusion of EBV-DNA is fascinating and a clear strength of this paper.  Given that the bloodtests were drawn serially, however, efforts should be made to clarify at what time point we are calling someone “EBV-positive”.  In addition, more space should be used to emphasize the most impressive finding on these survival curves – the absolutely shockingly poor outcomes among patients with EBV + disease posttreatment.  Again, though, does the EV+ in Figure 5 reflect EBV+ before or after treatment?
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: CLINICAL OUTCOMES OF RESIDUAL OR RECURRENT NASOPHARYNGEAL CARCINOMA TREATED WITH ENDOSCOPIC NASOPHARYNGECTOMY PLUS CHEMORADIOTHERAPY OR WITH CHEMORADIOTHERAPY ALONE: A RETROSPECTIVE STUDY
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper is well written and the conclusions reasonable.
Experimental design: The study design is effective and it is able to investigate the impact of EBV-DNA in patients' prognosis according to a subgroups stratification analyzing the stage of disease and the treatment strategy adopted.
Validity of the findings: Data is robust and statistically sound.
Additional comments: The paper can be improved by addressing these issues:
1) Please, specify in the material and methods section the histological subtype of nasopharyngeal cancer enrolled in this study. Only non-keratinizing carcinoma (WHO type III) have been included? I strongly suggest you to specify this information.
2) The results herein reported suggest that surgery was more effective than CRT at facilitating the reduction of EBV-DNA viral load and therefore surgical treatment has better therapeutic efficacy than CRT alone. (Discussion, lines 254-256). However, surgery is not feasible in every case of nasopharyngeal cancer recurrence (e.g. internal carotid artery encasement, massive intracranial
intradural involvement, orbital content invasion). I would like to suggest the Authors to improve the Discussion section by including the list of contraindications for endoscopic nasopharyngectomy currently accepted. In this regard, I suggest you to refer the study by Castelnuovo et al. where actual contraindications for salvage surgery in recurrent nasopharyngeal cancers have been clearly elucidated (Castelnuovo et al. Endoscopic endonasal nasopharyngectomy in selected cancers. Otolaryngol Head Neck Surg. 2013 Sep;149(3):424-30. doi:10.1177/0194599813493073)
3) A limit of this study is that patients have been allocated between the surgical and non-surgical group arbitrarily, without any randomization. The Authors should discuss deeply this and possibly propose future studies where a randomization can be introduced.


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: CLINICAL OUTCOMES OF RESIDUAL OR RECURRENT NASOPHARYNGEAL CARCINOMA TREATED WITH ENDOSCOPIC NASOPHARYNGECTOMY PLUS CHEMORADIOTHERAPY OR WITH CHEMORADIOTHERAPY ALONE: A RETROSPECTIVE STUDY
Review round: 1
Reviewer: 3

Output:
Basic reporting: The article contains several English irregularities, especially with the use of adverbs ( see examples in the revised PDF).  It would benefit from a revision by a native English speaker.
Overall, it is well organized and beautifully illustrated
Experimental design: The main flaw in this section is the lack of clarity about how the treatments were chosen.  It lacks a description of criteria used in each group.  There are other important data points missing (see revised PDF)
Include reason for death (local, loco regional, distant mets, side effects of treatment.
Validity of the findings: The analysis seems sound; however, the conclusions are flawed in view of the lax methodology, as described above.  They will have to be revised.
In addition, theaters fail to address complications from each approach of treatment.  This can also affect
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: COMPARISON OF HUMAN PAPILLOMAVIRUS (HPV) DETECTION IN URINE AND CERVICAL SWAB SAMPLES USING THE HPV GENOARRAY DIAGNOSTIC ASSAY
Review round: 1
Reviewer: 1

Output:
Basic reporting: Data regarding the worldwide and local epidemiology is missing.
Experimental design: In the statistical section there is no reference to sample size and power calculation
Validity of the findings: I suggest avoiding using phrases such as may be useful and could be accurate
when concluding.
Additional comments: I enjoyed reading the manuscript. It is well written and is quite clear.

"Urine samples processed with the HPV GenoArray assay may be useful for the clinical management of HPV infection and the technique could be an accurate, noninvasive method for monitoring HPV infections in women."
This sentence should be rephrased. The test does not change management. Something like - Urine sample with the GenoArray is an alternative for women declining to undergo PAP smear however now days and using current technology it is not the first line screening option.


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: COMPARISON OF HUMAN PAPILLOMAVIRUS (HPV) DETECTION IN URINE AND CERVICAL SWAB SAMPLES USING THE HPV GENOARRAY DIAGNOSTIC ASSAY
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is written clear english throughout following professional article structure.
Experimental design: Research question is clear, well defined, relevant & meaningful. However, as many controls are missing, the results do not fully support authors conclusion.
Validity of the findings: There is a minimal impact and novelty in this manuscript. Data are not robust and credible.
Additional comments: Developing a noninvasive HPV detection method may be useful and significant, particularly for people in developing countries. However, this manuscript by Nilyanimit et al. provide limited value.

The results of HPV prevalence in this study are not consistent with other previous studies. For example, the percentage of HPV16 positive samples is unusually low among the samples showing that less than 20% (12 out of 65) of HPV-positive samples have HPV16 DNA. As the authors did not use any positive and negative controls, it is concerned if the procedures and methods used here were appropriate.

Additionally, the overall concordance percentage (65.2%) between the cervical swab and urine samples is not impressive and thus, it is not sure the urine test that the authors suggest is useful at all.

It is impossible to understand what the authors exactly did in this study, because many important descriptions about experimental procedures and data are missing. The authors should explain in detail how they extracted DNA, normalized the samples, validated the assays and specimens, etc.


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: COMPARISON OF HUMAN PAPILLOMAVIRUS (HPV) DETECTION IN URINE AND CERVICAL SWAB SAMPLES USING THE HPV GENOARRAY DIAGNOSTIC ASSAY
Review round: 1
Reviewer: 3

Output:
Basic reporting: No comments
Experimental design: 1. It would make the paper stronger if the authors could show an alternate method for HPV detection other than the two they compare, which would show if the the HPV Genoarray is the most superior non-invasive method for detection.
2. It would also be interesting if the authors could discuss the rationale for choosing the current GenoArray method compared to other existing methods.
Validity of the findings: 1. It might be better if the authors can provide a clear gap in knowledge and state the necessity and importance of such a study.
2. The authors should also consider discussing the differences they observe with sensitivity to the other existing methods, since  these other methods are currently used as well. The authors have discussed the difference with the other GenoArray based study but not with studies involving other methods
Additional comments: The manuscript "Comparison of human papillomavirus (HPV) detection in urine and cervical swab samples using the HPV GenoArray Diagnostic assay" discusses the use of non- invasive methods for HPV detection, which is crucial given the rising incidence of HPV. The manuscript is well written and discusses the results and aspects of the assay in required detail. It might make the manuscript stronger to discuss the gap in knowledge with current HPV genearray studies and also discuss the differences seen compared to the other available methods as this might further highlight the importance of this 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: COMPARISON OF HUMAN PAPILLOMAVIRUS (HPV) DETECTION IN URINE AND CERVICAL SWAB SAMPLES USING THE HPV GENOARRAY DIAGNOSTIC ASSAY
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comments
Experimental design: No comments
Validity of the findings: No comments
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: COMPARISON OF HUMAN PAPILLOMAVIRUS (HPV) DETECTION IN URINE AND CERVICAL SWAB SAMPLES USING THE HPV GENOARRAY DIAGNOSTIC ASSAY
Review round: 2
Reviewer: 2

Output:
Basic reporting: No Comments
Experimental design: No Comments
Validity of the findings: An additional method of comparison might further validate the findings of the article.
Additional comments: While the authors have not provided any further experimental evidence to address the comments / concerns raised previously, they have addressed them in the discussion and via other textual changes.


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: HISTAMINE-2 RECEPTOR ANTAGONIST FAMOTIDINE MODULATES CARDIAC STEM CELL CHARACTERISTICS IN HYPERTENSIVE HEART DISEASE
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: Results seem like rather preliminary.

1. Provide representative images for figures 1a, 2a and 2c.
2. There is no mechanism explaining salutary effects of famotidine on CSCs. It would help if authors can provide a molecular basis for the observed effects.
3. Do CSCs express histamine receptor?
4. Authors note that histamine receptor is present primarily on mast cells, known to express c-kit. Can the authors provide results showing that their CSC population is negative for mast cells population tryptase.
5. What happens to wild type CSC proliferation and growth kinetics after treatment with famotidine in vitro.
Validity of the findings: The results are inconclusive and preliminary. More rigorous analysis required.
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: HISTAMINE-2 RECEPTOR ANTAGONIST FAMOTIDINE MODULATES CARDIAC STEM CELL CHARACTERISTICS IN HYPERTENSIVE HEART DISEASE
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is clear but unfortunately includes no raw data. All results are presented as graphs. The authors should provide representative images for all three groups for Figures 1A, 2A, 2B and 2C. Furthermore, flow plots should be presented to justify the claim that the cells were 92+/-3% ckit+ and negative for CD45 and CD31.
The introduction is brief but adequate. The discussion should include more examples of comparision between this work and what is known in the field.
Experimental design: The experimental design is sound but the details of the methods are somewhat brief. For example, were the explants plated on coated flasks, what medium was used, which antibodies were used for flow, what were the cells stained with in the colony forming assay, how was the cell number obtained for the proliferation assay?
Minor comment - what is 'Age associated variation in fig 1D?
Validity of the findings: It is hard to assess the data when no raw images have been presented. If all the results are confirmed by raw data then the conclusions are sound.
Additional comments: This is an interesting piece of work but is marred by the lack of raw data and the brief discussion.


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: HISTAMINE-2 RECEPTOR ANTAGONIST FAMOTIDINE MODULATES CARDIAC STEM CELL CHARACTERISTICS IN HYPERTENSIVE HEART DISEASE
Review round: 2
Reviewer: 1

Output:
Basic reporting: The manuscript is clear and significantly improved in the revised version.
Experimental design: The overall hypothesis is novel and interesting and addition of new methodology and results have improved the manuscript.
Validity of the findings: The findings are novel and well supported by the data.
Additional comments: The authors have addressed all the concerns raised.


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: HISTAMINE-2 RECEPTOR ANTAGONIST FAMOTIDINE MODULATES CARDIAC STEM CELL CHARACTERISTICS IN HYPERTENSIVE HEART DISEASE
Review round: 2
Reviewer: 2

Output:
Basic reporting: In this revision the authors now include improved discussion of their results and representative images to support their data. However, the images in figure 5 to show b-Gal staining and the Western blot in Fig 5E are not very convincing.
Experimental design: The methods are now improved with sufficient detail in most cases, although the quantities of FGF and insulin-selenium-transferrin are not given in 2.2
Validity of the findings: The data appears robust, although better images should be provided for fig 5 if possible.
Additional comments: The manuscript is much improved but requires some editing for English.


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: INFLUENCE OF EXERCISE DURATION ON CARDIORESPIRATORY RESPONSES, ENERGY COST AND TISSUE OXYGENATION WITHIN A 6 HOUR TREADMILL RUN
Review round: 1
Reviewer: 1

Output:
Basic reporting: Abstract:
Please insert the correct VO2max units throughout the manuscript:  "mL•min•kg-1" change to "mL•kg-1•min-1"

Since you did not directly measure beta-oxidation. I would change to a reduced RER. I would suggest the authors estimate fat oxidation with the use of RER, and Oxygen Utilization.

If you observed an increase in VO2 at the 10 km/h running speed, this would indicate a reduced running economy, despite no change in the energy cost of running.

Introduction:
Line 52. "It has been suggested increases".... Change to "It has been suggested that increases..."

Did you record years of training experience? Or average weekly training time? These are often more informative then VO2max values.

Was nutrition monitored or recorded? I know it was not controlled. But nutrition could have had a large effect on the results.

Line 156-157. RER is VCO2:VO2. You have it reversed? Please correct.

I am not clear how you obtained J•kg•m-1 . Can you please show me how you got these units?

It is unclear why the two-way RM ANOVA and three-way RM ANOVA's were used. These were not clear from the aim of the study.
Experimental design: I completely understand the small sample size, but was a sample size calculation done prior to the study?
Validity of the findings: Was the metabolic system calibrated before and after? What is the reliability of the metabolic system in the laboratory used?
Additional comments: The study is very unique, with a 6 hours of treadmill running. The authors point out on several occasions that no downhill running was included as this may alter the findings. However, what is the external validity of such findings (ie. are there any ultramarathon courses with no downhill sections)?

I also feel that is important to point out that running economy was reduced despite no change in the energy cost of running.

Lastly, I suggest the authors calculate fat oxidation instead of assuming a reduction in RER is equivalent to an increase in beta-oxidation.


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: INFLUENCE OF EXERCISE DURATION ON CARDIORESPIRATORY RESPONSES, ENERGY COST AND TISSUE OXYGENATION WITHIN A 6 HOUR TREADMILL RUN
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: Speculation is welcome, but should be identified as such.
Additional comments: General comments: The current paper is relatively well-written and the topic related to endurance exercise and including many laboratory-running measurements is quite interesting. However, the paper requires some important clarifications, especially during the methods and discussion parts. To improve the global reading of the present manuscript, it would be judicious to use more abreviations throughout the text, such as 10-CR or HILL from the beginning to the end of proposed statements. The authors are requested to improve the quality of their work by taking account into the specific comments described below.

INTRODUCTION:

.	L46: suggestion:  Maximal oxygen uptake (VO2max), the fractional rate of  VO2max (%VO2MAX) and the energy cost of running (Cr), i.e. the submaximal metabolic demand (VO2) per unit of distance covered are…
.	L48: Insert “may be” instead of “are” affected
.	L52: Insert “that” after suggested.
.	L53-56 : The reviewer is in agreement with the statements used by the authors but the sentence needs to be re-written by presenting firstly the effects of exercise duration until 8-h on VO2 and secondly, the effects of ultramarathon on the same variable.
.	L56-61 : Could you reformulate these sentences please.

METHODS :
Could you extend or precise the weekly running mileage for your experimental group. Does your population cycle during their training sessions ?
L111: Replace maximum VO2 by VO2max.
L132 : Why did you select a +10% slope ?
L133 : For HILL, is the speed corresponding to 70%VO2max or the highest possible speed as you reported in the manuscript ? clarify the confusion please.
L160 : It would have also been interesting to convert J.kg-1.m-1 in J.m-1 shunting the body mass which may decrease with exercise duration and exert an additional influence on final CrJ values. What ‘s your position about this choice of unit.
 L176 : What was the average time to attach and remove the NIRS devices during the four modules ? Could you provide more details about the position of the NIRS device on the prefrontal cortex.

RESULTS : well presented.

DISCUSSION : in the paragraph 17, I suggest that you also present the results including oxygenation and metabolic responses, not only PCI and RPE.
L245-246 ; precise the two exercise intensities.
L250- : Could you reformulate this sentence (i.e. repeated terms) and by including RER values to characterize the beta-oxidation.
L253 : Could you reformulate « at intensities < 80% of maximum ».
L257 : Beta-oxidation is not directly measured in the current work but extrapolated from RER values. It should be more appropriate to use the RER decrease firstly before inferring on beta-oxidation.
L263 : replace « mild » by small.
In the paragraph 19, the authors discussed their results focusing on the lack of CrJ alteration with exercise duration. Some hypotheses are proposed but the training status of the experimental group has not discussed in this part. The high training background and thereby, muscular adaptations in ultramarathon runners might constitute an additional hypothesis to explain the lack of CrJ alteration with exercise duration, either on level ground or HILL condition. Could you explore this type of hypothesis.
You observed an absence of CrJ alteration on level ground, but at a moderate intensity (10 km/h) or at a self-selected speed or both. Could you precise in the discussion part what « level ground » means to clarify the reading. Furthermore, for the self-selected speed-based period of measurement, you observed a decrease in running speed across the modules and this decrease in speed may explain why CrJ did not change across the time in the case where VO2 continuously increase. You have not discussed the ratio between change in VO2 and change in speed to explain CrJ responses across the time.
L283-286 : could you reformulate this sentence.
L290-295 : The authors hypothesized that it is likely that the exercise duration during the HILL and 10-CR modules was too short to induce any significant changes in TSI responses throughout muscular sites. A link with a 24-h outdoor exercise using biopsies methods has been used, but it would have been better to create a link with studies investigating the evolution of NIRS parameters with exercise duration. Furthermore, it would be interesting to present limitations of NIRS devices in dynamic exercices in an attempt to explain the lack of TSI changes with exercise duration.
L312 : I am a bit confused when the authors reported that the 6TR did affect the energy cost of running.
Conclusions : insert future research directions at the end of conclusion part.

Title table 1. Heart rate is mentioned twice. Change heart rate relative to individual maximum. What is the signification of the statistical symbol used ? Which difference ?  Could you apply these modifications to table 2 and table 3.
Figure 1. Could you insert the abreviations 10-CR and HILL, moderate and heavy exercises in the figure content
In the results section, you wrote that TSI responses were significantly higher in PFC compared to VL and GL, but when observed the figure 3 and especially B and C, the reviewer has the impression that no difference exist between sites. Given that this impression is purely visual, could you confirm the statistical inference of your results. I suggest that you also change the statistical representation, not really clear.

.


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: INFLUENCE OF EXERCISE DURATION ON CARDIORESPIRATORY RESPONSES, ENERGY COST AND TISSUE OXYGENATION WITHIN A 6 HOUR TREADMILL RUN
Review round: 1
Reviewer: 3

Output:
Basic reporting: -This is a nicely written manuscript that is clear in its rationale, methods, analyses, and conclusions. No major concerns.
- No notable grammatical issues.
- Data is nicely presented.
Experimental design: - The design is appropriate for the research question.
- Hypotheses are appropriate and rationalized.
- Methods are nicely described - no concerns.
Validity of the findings: - The findings are interesting and worth publishing. I'd suggest linking the data with work showing the effects of prior heavy exercise on moderate intensity exercise (references noted below).
- Statistics are nicely described.
Additional comments: - Please define "reverse cardiovascular drift".
- Would suggest inclusion of some priming literature on the amplitude of VO2 -- as these studies provide some physiologic insight into the mechanisms of how prior heavy exercise influences subsequent moderate intensity exercise (DiMenna et al. J Appl Physiol 2009 107(6):1743-56; Wilkerson et al. J Appl Physiol. 2004 97(4):1227-36; Gurd et al. J Appl Physiol. 2005 98(4):1371-8). These seminal papers highlight important physiology about priming effects on VO2.
-


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: INFLUENCE OF EXERCISE DURATION ON CARDIORESPIRATORY RESPONSES, ENERGY COST AND TISSUE OXYGENATION WITHIN A 6 HOUR TREADMILL RUN
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: clear
Validity of the findings: clear
Additional comments: Responses and/or modifications from the authors are considerably improved the manuscript in terms of methodological quality, results and discussion presentation. I recommend the publication of the current work in the Running scope, when applying the minor specific comments below.

L50: ….that increases in Cr correlate positively with….

L54: remove “s” : afetr a 65-km trail ultramarathon

L54: suggestion : Similarly, following a 65 km mountain ultramarathon….

L132: I suggest authors to report why the +10% slope was selected in this protocol, on the basis of feedback comments.

Paragraph number 7: I suggest authors to remove “complete”  (repeated twice) in the following sentence…. to complete the condition and/or (HERE) the 6TR,....


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: INFLUENCE OF EXERCISE DURATION ON CARDIORESPIRATORY RESPONSES, ENERGY COST AND TISSUE OXYGENATION WITHIN A 6 HOUR TREADMILL RUN
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors have addressed my comments.
Experimental design: The authors have addressed my comments.
Validity of the findings: The authors have addressed my comments.
Additional comments: The authors have addressed my 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: INDEPENDENT EVOLUTION OF TETRALOOP IN ENTEROVIRUS ORIL REPLICATIVE ELEMENT AND ITS PUTATIVE BINDING PARTNERS IN VIRUS PROTEIN 3C
Review round: 1
Reviewer: 1

Output:
Basic reporting: The language used by Prostova et al. in their paper is clear and unambiguous, yet I would like to recommend a further checking to improve wording/phrasing in some sections to improve the overall readability. Some specific notes on this regard:
Line 43: I suggest adding long at the end of the sentence  “… with plus strand genome about 7500 nt long”
Line 60: I suggest changing "leafs" to "leaves"
Line 69: I suggest changing "extremal" to "extreme"
Line 107: I suggest changing "formed" to "created"
Lines 119-122: I suggest expressing the total sequences per organism in the clearer format organism (N total)
Line 144: I suggest changing "conservative" to "conserved"
Line 299: please remove the comma
Line 398: I would say that data "suggests" rather than "demonstrates"

Overall, the submission is ‘self-contained’ with a clear aim and clear results, which can be used for future experimental validation of the hypothesis made by the authors in the paper.
The authors made a good job in properly referencing and giving relevant background to their work. Their paper conforms to the journal guidelines, figures are clear and the raw data is appropriately given as supplementary material. To improve their manuscript, I would like to suggest to the authors to expand the Conclusions section to include more details on the final message of their paper.
Experimental design: The work successfully qualifies for the Aims and Scope of the journal, conveying new findings on a relevant biological system using widely known bioinformatics techniques. The research question is well defined in the first sections of the paper, with several mentions of the significance of their study from various biological points of view. However, I wish the authors would put more emphasis on how their study contributes to fill the knowledge gap they are trying to address.
The methodology used and described in the paper is sound enough to support their conclusions, though I would suggest to the authors to give more details on some methodological approaches that can be relevant to make their work reproducible. For instance in line 94 the authors report they used Clustal for sequence alignments, but without giving more details on the parameters that have been used (and if they differ between RNA and protein analysis). Another example is in lines 113-114 where the Vienna RNA Websuit has been used for secondary structure fold. I suggest adding some more details about the algorithm and parameters that have been used.
Validity of the findings: The data presented by the authors are clear and robust, which support their conclusions. The speculative part is somewhat limited and identified as such, without falling in a common pitfall in this type of study of over interpretation of raw bioinformatics data to extract stretched biological meanings. A note I wish to make to the authors is that starting from line 312 in the Discussion they highlight how their data suggest a recognition structure-based rather than sequence-based, which to me is worth to be mentioned again towards the Conclusions part, being a significant result for general macromolecular recognition rules.
Additional comments: All things considered, the work by Prostova et al. is in my opinion suitable to be published in PeerJ and can be further improved with some minor revisions/improvements I mentioned in the previous sections


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: INDEPENDENT EVOLUTION OF TETRALOOP IN ENTEROVIRUS ORIL REPLICATIVE ELEMENT AND ITS PUTATIVE BINDING PARTNERS IN VIRUS PROTEIN 3C
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall the paper is clear and there are no widespread severe language issues present. However, there are some small grammatical and wording issues. I have listed a few example below.

1. On line 69 the phrase 'extermal stability' should be 'extreme stability'.

2. On line 215: 'the conservative motif KFRDI' should be 'the conserved motif KFRDI'.

3. On line 228: 'tripeptide (position 155) was invariantly Gly.' should be 'tripeptide (position 155) was always Gly.'

This is not a comprehensive list of all such issues. Overall the paper could use some small editing for these minor wording issues.

The introduction and background provide a clear summary of the subject and enough context to understand the question being asked. In addition, the paper is well structured and organized. The paper as a whole is an easy read.

In addition the figures are generally good. Figure 1 is very helpful for understanding the biological context of the research and Figure 2 helps in understanding the finer details of the loop in question. However, there are some issues with Figure 3. They are:

1. Part A of the figure may best be presented as a simple table. This would give more complete information to the reader as it would be easier to see the exact counts of type of loop.

2. Part B needs some modifications. The arrows in B that indicate the important positions in the protein are very helpful it would be ideal if the number in the sequence logo was consistent with the stated numbers. That is the position labeled with 'proteolytic Glu 71' should be number 71 instead of 2. Finally, it would be helpful to label the arrow in the lower right as Lys153 from Rhinovirus A as it is not clear that that motif is from Rhiovirus A.

Overall, the paper is well presented but some edits are necessary.
Experimental design: The authors aim is to find a correlation between sequence conservation of domain d loop regions in Enteroviruses and the interacting amino acid sequences from protein 3C. They used a simple straightforward method to find any correlation. The methods section explains much of the techniques used. However there are some issues with their methods:

1. They do not justify the inclusion of otherwise excluded loop sequences in their analysis. For example, on line 171 the authors mention adding 3 unique tetra loop sequences back into the data set after filtration. I suspect this is to maintain diversity of loop sequences from the species. However, there is it is not clear to me why this must be done. The reasons for this decision must be clearly justified in the text. In addition, I would be interested to know if their conclusions change when these sequences are included.

2. They use a 99% percent cutoff and claim that a 95% cutoff results in a 'dramatic loss of unique tetraloop variants', providing a number of sequences lost would help justify the selection of 99% cutoff.

In summary, I believe their methods are correct but some details require explanation.
Validity of the findings: The authors conclusions about lack of a relationship between the sequence conservation in the domain d loop and the interacting protein are well supported by the data. As they state there is no clear pattern of loop sequence to protein sequence conservation. In addition, their observation that the protein sequence appears to be more diverse than the RNA sequence is both interesting and supported. The authors may wish to emphasize this contrast more.

However, the authors may be underestimating the degeneracy of the sequence to structure relationship. In Petrov et. al (doi:10.1261/rna.039438.113) it was found that some loops may differing sequences as well as number of nucleotides but form the same overall 3D structure. Observations such as this strength the their conclusions and the authors may wish to cite such work.

In addition, there has been some work studying the structure RNA/protein interactions. The authors may want to review this literature to suggest a how the diverse protein and loop sequence interact. If their suggestion that the overall 3D structure is maintained then the interaction should also be maintained. This may be outside the scope of the current work and I understand if the authors wish to leave such work for another publication.
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: INDEPENDENT EVOLUTION OF TETRALOOP IN ENTEROVIRUS ORIL REPLICATIVE ELEMENT AND ITS PUTATIVE BINDING PARTNERS IN VIRUS PROTEIN 3C
Review round: 1
Reviewer: 3

Output:
Basic reporting: The study is well-conducted and detailed. I have only few minor comments that might clarify the manuscript.

1) Table 2: It would be more clear if proportions of loop sequences instead (or in addition) to occurrence was indicated in the heatmap (i.e. percentage of a given loop sequence out of sequences observed in a given virus species).

In addition, it would be interesting to see if there are statistically significant differences in the proportions of a given loop sequence between virus species.
For example, loop sequence CUCG seems to be prevalent in EV-A species, but not in EV-B and EV-C species.

Table S1 contains more information than Table 2 (regarding dataset bias - i.e. predominance of EV-A71 and PV), therefore I would prefer showing Table S1 in the main article.

In Table S1, it would be more clear if two more columns; 'non-A71 EV-A' and 'non-polio EV-C' would be included.  This would help the reader to understand the structure of the data (i.e. how much of the diversity in 'all' column is explained by EV-A71 and PV).

2) Fig 3: Only five species are shown - should others be included? e.g. rhinovirus B (with triloops) would be informational.

3) Supplementary Tables:

Should  protein 3C tripeptide sequences be also given for EV-B, EV-D, EV-E, EV-F and Rhinovirus B?
Experimental design: no comment
Validity of the findings: 1) Page 13 line 164-165:
"Interestingly, the diversity of tetraloops among EV71 serotype was similar to the diversity of tetraloops in the whole Enterovirus A species (Table S1)."

This statement needs clarification. According to Table S1 it seems that some tetraloops (such as UUCG, UAAG and UGAG) are found only in EV-A71 type but not in the other EV-A types.On the other hand, tetraloop UGCG seems to be highly prevalent among other EV-A types (N=112), but rare among EV-A71 (N=2), whereas CUCG seems to be prevalent among EV-A71 (N=127) but rare among the other types (N=5).
Additional comments: Generally, the study is well-conducted and detailed. The conclusions are supported by the data. I have only few minor comments that might clarify 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: BENCHMARK DATASETS FOR PHYLOGENOMIC PIPELINE VALIDATION, APPLICATIONS FOR FOODBORNE PATHOGEN SURVEILLANCE
Review round: 1
Reviewer: 1

Output:
Basic reporting: There's no question about basic reporting in this manuscript. Professional English is used throughout, sufficient background is provided, and the structure is professional and the manuscript self-contained
Experimental design: Manuscript adheres to Aims and Scope. The research question is well defined and relevant, and the investigation has been performed to high technical and ethical standards.
Validity of the findings: The findings are valid and the manuscript adheres to PeerJ's standards
Additional comments: I think it’ll be helpful if the authors add information as to how they determined that the bacterial isolates are epidemiologically linked and in what direction. One key issue is establishing a phylogenetic relationship among isolates that mirrors the transmission network. I understand this is straightforward for the simulated data but it’s not clear to me how this was done for the real biological data.

I mention this because the equivalency of phylogenies to transmission trees has been somewhat controversial (e.g., PMID: 24037268; PMID: 24675511; PMID: 26230489; PMID: 24916411). Consequently, methods has been develop to directly address this issue, e.g., PMID: 28545083

One minor thing that's hanging in my head is why providing example datasets in xlsx if the script takes tsv’s? The conversion is trivial but keeping everything tidy in open formats has its advantages.


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: BENCHMARK DATASETS FOR PHYLOGENOMIC PIPELINE VALIDATION, APPLICATIONS FOR FOODBORNE PATHOGEN SURVEILLANCE
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall, the manuscript was well written. It is unclear why so many references are applied to the reference of Lyve-SET. I would just cite the manuscript that describes the pipeline, unless you are citing the specifics of diverse projects where Lyve-SET has been used.  The NASP pipeline was mentioned, but wasn’t cited.

L95: Peptoclostridium is not really used and is immediately followed by Clostridium in your text. GenBank currently uses “Clostrioides”.
Experimental design: This manuscript describes a method to download and compare pipelines for WGS analyses. However, after downloading the repository, I saw no script referred to as “Gen-FS Gopher” or “GG”.  There appears to be no comprehensive, documented workflow on how to download the 5 test datasets. The scripts provided to convert between “xlsx” and “tsv” required extra dependencies and I could not get them to work. Saving them as tsv files seemed to work and I was able to download the datasets, although I received an error.

If these are benchmarking datasets, which SNPs should consistently be called? Simply obtaining the same tree doesn’t mean that any given pipeline is calling the correct SNPs. Why not release the SNPs that were used to infer the provided tree? As it reads now, it is unclear if the true utility of this paper is in benchmarking, or providing a tool to interface with the SRA to grab sequences and trees.
Validity of the findings: Having a standard benchmarking scheme would be very helpful to standardize analyses across computational pipelines. Additional work on the repository associated with testing your scripts on multiple platforms and adding additional documentation would help users not familiar with these types of pipelines. Additional text on how these datasets can be used to benchmark pipelines would also help users assess new pipelines, using metrics that can be directly compared.
Additional comments: This manuscript could be improved by working on the documentation, making sure that script names in the manuscript match those in the repository, and by providing specific metrics that users could use to assess new SNP pipelines. Providing standardized datasets to the community would be very helpful.


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: BENCHMARK DATASETS FOR PHYLOGENOMIC PIPELINE VALIDATION, APPLICATIONS FOR FOODBORNE PATHOGEN SURVEILLANCE
Review round: 1
Reviewer: 3

Output:
Basic reporting: This article is generally clear and well written and the impact of the work is communicated clearly. Data and programs were accessible as indicated in the text.

I found that the text was not clearly organized into Introduction/Materials and Methods, Results and Discussion. For example, the last paragraph of the introduction seems to be materials and methods. Some of the information on lines 102-112 (e.g. selection of datasets, data simulation) should be integrated into the materials and methods. Similarly, description of data simulation (lines 148-160) and the description of the development of the GG script also seem to fit within the scope of materials and methods. Authors should consider modifying organization and perhaps combine results/discussion. Given that the topic of this paper is somewhat different than a traditional scientific paper (announcement of the availability of data/tools rather than an evaluation of performance), perhaps traditional subheadings are not appropriate.

Some minor comments:
The Gen-FS gopher script is called “downloadDataset” on the github site which may lead to confusion.

The pages preceding the tables are confusing. Eg:Table 2 “ Reviews and evaluates data submissions in food and color additive petitions and premarket notifications (GRAS and Food Contact Surfaces notifications) to determine the safety of the use of a product in
foods within the context of applicab”

Line 27: ortholog determination (no hyphen)
Line 28: single-nucleotide polymorphisms
Line 60/71: publically (should be publicly as in line 37?)
Line 73: update number of genomes if possible
Experimental design: The design of the study is clearly described.

I would be interested in results of analysis of this dataset with different phylogenetic pipelines that are currently in use among Gen FS partners to demonstrate how data generated from this dataset would be interpreted.

Given that reference genomes are provided, could SNP/SNVs locations be identified?

It would also be appropriate to provide a figure showing phylogenetic trees.
Validity of the findings: no comment
Additional comments: This manuscript describes the development of benchmark NGS datasets for priority foodborne pathogens that can be used to evaluate the performance of phylogenomic pipelines, and addresses the development of standardized formats for submission of similar benchmark datasets in the future. This work represents an important contribution that will be particularly useful for regulators in determining the reliability of new phylogenomic pipelines applied to the surveillance of foodborne pathogens. The tool for rapid retrieval of validation data will be useful in providing easy access to this data.