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: HABITAT USE, PREFERENCE, AND UTILIZATION DISTRIBUTION OF TWO CRANE SPECIES (GENUS: GRUS) IN HUIZE NATIONAL NATURE RESERVE, YUNNAN–GUIZHOU PLATEAU, CHINA
Review round: 1
Reviewer: 2

Output:
Basic reporting: In general this paper is written in a way that is understandable but has a couple areas of improvement and expansion.
Experimental design: The methods section of this paper need improvement and expansion which have been capture in the attached track changes.
Validity of the findings: Results need to be expanded and certain areas of the discussion need work.
Additional comments: In general the paper is written well but could be improved with some expansion and recasting. In the end the paper will help inform conservation within the area but the story you have laid out lacks some details to holistically tell that story and identify those conservation needs.


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: HABITAT USE, PREFERENCE, AND UTILIZATION DISTRIBUTION OF TWO CRANE SPECIES (GENUS: GRUS) IN HUIZE NATIONAL NATURE RESERVE, YUNNAN–GUIZHOU PLATEAU, CHINA
Review round: 1
Reviewer: 3

Output:
Basic reporting: In general the manuscript is well presented, with a professional article structure which is set out logically. However, the rationale for carrying out the study could be developed more clearly. In the current version of the manuscript the knowledge gap is not identified clearly. Without this rationale, it will be hard for the reader to understand why the study has been carried out in the way it has. The authors state on on lines 71-75 that information on habitat use and distribution are needed to "put forward more rational and effective habitat management", but no information is presented on current habitat management and why this is ineffective, or why information on habitat use and preferences will help to address the knowledge gap. Some of the text currently in the methods section (e.g. lines 138-143 and 156-158) should be moved to the introduction and used as part of an improved rationale for the study.

The manuscript contained some spelling and grammatical errors, and so I recommend that the authors consult a native English speaker to correct these. I have listed a few examples below, but there are many others:
- line 49: "migrants" not "migrators".
-line 72: "measures" not "measurements".
- line 249: "segregation" not "segregating".

There were a number of instances where the citation of additional literature would add useful additional detail or clarification to the manuscript:
- lines 46-48: Is there a reference to the Biodiversity Red List of China that can be cited?
- lines 71-72: You do not say why information on habitat use and preferences will help to "put forward more rational and effective habitat management". There are previous studies of waterbird habitat use and preferences that you could cite to help develop your argument, e.g. Wood & Stillman (2014) Do birds of a feather flock together? Comparing habitat preferences of piscivorous waterbirds in a lowland river catchment. Hydrobiologia (2014) 738:87–95. DOI 10.1007/s10750-014-1921-6
- lines 150-154: If you decide to use the simpler method of estimating habitat preferences, this is the original reference for Ivlev's electivity index: Ivlev, V. S. (1961). Experimental ecology of the feeding of fishes. Yale University Press, Connecticut.
- lines 174-179: To aid with the statistical analyses, I have recommended reading and citing the following paper: Zuur, A. F., E. N. Ieno & C. S. Elphick, 2010. A protocol for data exploration to avoid common statistical problems. Methods in Ecology and Evolution 1: 3–14.
- lines 174-179: If you choose to retain modified versions of the statistical analyses that account for the sources of pseudoreplication, then I recommend citing the following paper in your explanation: Hurlbert, S. H. (1984). Pseudoreplication and the design of ecological field experiments. Ecological Monographs, 54, 187-211.
Experimental design: In my view the manuscript certainly represents original primary research that falls well within the aims and scope of PeerJ.

As mentioned above I felt that the rationale for carrying out the study could be developed more clearly. I also had more substantial concerns regarding the data collection and calculations:

1) Field surveys
The description of the methods could be improved, as the current version of the manuscript omits many details which are required to evaluate the study. Whilst the length of the transect is given (line 112), the width of the transect is not. What area either side of the transect was surveyed? Were the 12 surveys spaced out equally across the study period?

2) Habitat preference calculations
There are many different available indices of preference, and so it is important to explain the choice. Why was the ranking matrix used rather than the simpler electivity index proposed by Ivlev (1961)? The Ivlev electivity index is particularly useful as it presents values on a scale of -1.0 (total avoidance of habitat type) to +1.0 (exclusive use of habitat type) which is widely understood and easy to interpret, and this is what I  recommended that you use in your study. If you wish to use a more complex method, you should give compelling reasons for doing so. Furthermore, in calculating habitat preferences it is important that the area of habitat used to estimate habitat availability matches the area used to determine the habitat use of the birds. However, it is not clear from the methods reported here whether this was the case. Finally, reporting single values of habitat use and preference ignore the variance between the 12 surveys. Instead, mean values with 95% confidence intervals would be much more useful than the single values for habitat use and preference that are currently presented. These mean +/- CI habitat use and preference values would be more effectively displayed in figures rather than in tables, as figures would allow the differences between habitat types and species to be visualized more easily.
Validity of the findings: In general I felt that the discussion was well written, with appropriate references to the key findings and their context. As I have recommended a number of changes to the analyses, some of the conclusions may change as the manuscript is revised.

Statistical analyses
This section requires much additional detail in order to allow the reader to understand what was done and why. What parametric tests were used, as none are mentioned after line 174?
In lines 174-177 you state that you assessed whether your data conformed to a normal distribution. However, this is not the correct procedure. The parametric tests that you mention assume normality of the test residuals, not the raw data. Therefore, it is the residuals that need to be tested for normality. Many parametric tests make other assumptions that must be met, for example homoscedasticity. Were these assumptions also tested? I recommend the following paper on approaching statistical testing: Zuur, A. F., E. N. Ieno & C. S. Elphick, 2010. A protocol for data exploration to avoid common statistical problems. Methods in Ecology and Evolution 1: 3–14.
It was not clear to me what questions were being tested in the analyses mentioned here. I recommend revising this section to state the purpose of each test, including which dependent and independent variables were included.
The testing of the effects of (i) elevation, (ii) distance to roost, and (iii) flock size is problematic, as it was not properly introduced in the manuscript and there are issues of pseudoreplication (sensu Hurlbert 1984) that are not addressed. For example, the data combine 12 surveys of the same study area. Because the 12 surveys are of the same area (and presumably contain many of the same flocks) each survey cannot be considered to be independent. There is nothing reported in your manuscript that tells the reader how you addressed this problem. All of the data cannot simply be combined into a single analysis.If you wish to keep this section, then the analysis must be properly introduced and properly carried out. The sources of non-independence must be accounted for, perhaps via a repeat measures ANOVA or a mixed-effects model with survey data modelled as a random effect. The precise method that will be most appropriate will depend on how well the test assumptions are satisfied.
Finally, when conducting multiple tests and assessing significance via P values, you must correct your P values for multiple comparisons to maintain the level of alpha at 0.05. I recommend using Holm-Bonferoni adjustments to your P values; I calculated the adjusted P values the 7 values that you present in lines 189-194, and found that while all othe highly significant results remained <0.001, the values of 0.032 and 0.045 both became 0.064 (i.e. they became non-significant).

There were a number of other areas in which I felt that the manuscript could be improved:
The individuals within flocks are non-independent, and so basing your calculations of habitat use and preference on flocks seems reasonable. However, it would be valuable to be able to see how many individuals were using each habitat type, to provide the reader with useful information on the numerical importance of each habitat type. Perhaps this could be included in Table 1?
The percentages associated with the flock field utilization values are presented to too great a level of precision given the methods used; presenting these values to one decimal place would be sufficient. The same comment applies to the values reported in Tables 1, 2 and 3.
Additional comments: The manuscript contains many interesting ideas and I enjoyed reading it. You will see from my comments in the previous sections that I felt that there were a number of areas where the manuscript would be improved by revisions, in particular to the analytical methods. Whilst I know that such a large number of comments will always seem disheartening at first, I hope that I have explained adequately why I felt that each of the changes was necessary, and why I think that it will ultimately make your manuscript better. I hope that you will find my comments useful in improving your 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: HABITAT USE, PREFERENCE, AND UTILIZATION DISTRIBUTION OF TWO CRANE SPECIES (GENUS: GRUS) IN HUIZE NATIONAL NATURE RESERVE, YUNNAN–GUIZHOU PLATEAU, CHINA
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: I have now read the revised version of the manuscript. This revised manuscript represents a great improvement on the previous version. In my view all of the points raised in the earlier reviews have been addressed adequately and I have no further comments on the study. I would like to thank the authors for their efforts in carrying out a thorough revision, and in particular for incorporating the suggested changes to their analysis.


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: MARINE CYANOLICHENS FROM DIFFERENT LITTORAL ZONES ARE ASSOCIATED WITH DISTINCT BACTERIAL COMMUNITIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: This is an overall interesting study. The paper is well written and the sections are clearly organized and presented. The amount of data and results is good.

The result that “real marine” lichens (here two species of Lichina) have a microbiome that is more distinct from the “semi marine” Xanthoria, than "semi marine" Xanthoria to terrestrial Collemataceae is interesting. The comparison of the bacterial communities between the different species is interesting, and the high abundance of thermophilic/radiation-resistant species in the marine lichens is interesting and could help explain their resistance to quite extreme and unusual conditions. This result might be the highlight of the paper. It is also interesting that the microbiome of marine lichens may show more similarity to the microbiomes of marine algae than terrestrial lichens.

However, the aim of the article is to compare marine lichens' microbiomes to semi- and non-marine lichens', which brings to what is, to me, the main weakness of the study: all marine lichens tested in this study are members of the class Lichinomycetes, whereas all other tested lichens belong to the Lecanoromycetes (they are in fact very distantly related), and moreover all terrestrial lichens belong to the same family (Collemataceae). It is therefore difficult to tease apart the influence of the ecology versus the influence of the taxonomy.

The sampling design doesn’t help to tease taxonomy and ecology apart, because all the Lichina were collected in a single region (whereas Xanthoria was sampled in two different areas; it is a little strange to sample the species that are the main focus of the paper less than others).

This doesn’t mean that the study is not worthy of publication, especially because fixing this problem would require to start from scratch, but this bias should be clearly explained in the discussion. It is unfortunate that taxonomic relationships in the paper are either ignored (the Lichinomycetes vs, Lecanoromycetes situation is never discussed) or wrongly inferred (as for the relationships inside Collemataceae).

---

Indeed, the authors don’t take into consideration the revision and actual classification of Collemataceae (three of the four species sampled have been transferred to new genera), which led them to wrong assumptions on the relationships between the four Collemataceae sampled (the three “Collema” are not more closely related to each other than to “Leptogium” lichenoides)

The authors need to read the paper by Otalora et al. 2013 on the phylogeny of the Collemataceae “A revised generic classification of the jelly lichens, Collemataceae” published in Fungal Diversity.

In fact, Collema auriforme is now Lathagrium auriforme. Collema crispum is now Blennothallia crispa, Leptogium lichenoides is now Scytinium lichenoides.

As a consequence, the sentence “The bacterial communities associated with C. auriforme were actually more closely related to those of L. lichenoides than the other two species of the same genus, C. crispum and C. flaccidum that formed a separate cluster.” doesn’t actually make sense because Collema and Leptogium in the sense they are used in this current form were two polyphyletic genera.

Therefore, C. crispum (now Blennothallia crispa), C. flacidum (still a Collema s. str.) and C. auriforme (now Lathagrium auriforme) are not more closely related to each other than to L. lichenoides. I suggest removing the part comparing the three Collema vs. Leptogium, or changing it to reflect the actual phylogenetic relationships. The two most closely related species are actually Scytinium lichenoides and Lathagrium auriforme, which is in agreement with your results. They then share a common ancestor with Blenothallia crispa, whereas Collema flaccidum is the least closely related taxon.

By the way, it would be good to know how those lichens were identified. Was their identity checked with ITS or were they identified solely based on morphology?

It would also be good to know to which species of Xanthoria the collected thalli belong.

---

Methods and analyses are adequate for the hypotheses tested. The amount of contamination in the Miseq run (0.5% of contamination) is concerning but the authors seem to have taken much care in processing the data. The number of species tested is low, but the results are interesting nevertheless.

When the authors discuss the relative abundance of the OTUs, it should be emphasized that the sensitivity and specificity to primers, the quality of the DNA and other factors can favor the amplification of some groups over others. For example, the discussion in lines 572-579 doesn’t take into consideration the fact that this could be a product of the sequencing itself, rather than an actually difference in the thallus, as those lichens have different photobionts and different bacterial communities that may be differentially sequenced by the method.

The authors go very fast on the cyanobacterial result. It is not clear if it is for the marine or the terrestrial lichens that up to 10% of cyanobacterial sequences were not from the photobiont. The number for the other category should be indicated as well. Authors should also say something about the sequence diversity for the photobiont themselves (only one genotype? Several?) and discuss the genera that was found in the non-photobiont sequences.

In the section “Comparison to previously cultured strains from coastal lichens and C. auriforme”, authors should give more information about the specimens from which previous culture-based methods were applied. For example, do they come from the same locality? We should know relevant information about those other specimens without the need of reading other papers. Also, why was Roccella included in the comparison if it was not sequenced in this study?
Additional comments: Abstract: Illumina should be capitalized

References are not formatted the same way: for examples references in lines 49, 55 and 56 have three different formats

Line 260: the authors go from a description of the results on the mock sample (up to line 259) to the description of other samples in line 260, but don’t say clearly what they are describing. Is it a total number of OTUs for everything? Does it include the mock sample? Is it only for the Lichina? The part between lines 260-270 needs to explain more carefully to which sequencing those results correspond.

Line 271-274. The authors define many terms that are confusing if the reader doesn’t go back to this paragraph every time. For example it is not intuitive that inland lichens and terrestrial lichens are different concepts. Is it really needed to use those terms? I feel these categories are not needed (they are not often used in the rest of the text).

Line 42:  "to" is repeated twice, it should be “to which they are subjected daily”
Line 45: the word already is very oddly placed here
Line 49 needs a comma after the reference
Line 241: “terrestrial lichens were subject of blastn queries” I think should be “were subjected to blastn queries”
Line 326 show should be shows
Line 330: at least one comma is needed after sequences, but I would suggest splitting these long sentences in a few distinct ones.
Line 370  when the authors say “the OTUs consistently shared within the genus” but are only comparing two species in the genus, they can say “consistently shared between the two species” but cannot extrapolate to the entire genus.

Line 399 and around: What is called a core OTU should be clearly defined. What a dominant OTU is should also be defined.

Line 457: this communities should be these communities

Sometimes there is no space between the genus and species e.g., L.confinis in the caption of figure 6, sometimes Lichina is not italicized, please check carefully through 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: MARINE CYANOLICHENS FROM DIFFERENT LITTORAL ZONES ARE ASSOCIATED WITH DISTINCT BACTERIAL COMMUNITIES
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment.
Additional comments: Interesting and important study!

As there are so many aspects to cover it is difficult to refine these types of manuscripts into an informative and easily understandable form - I think the authors have done a fine job!

One could always argue for adding info on this and that issue but that would necessarily increase overall length.

However, maybe some more detail could be added to further emphasize the phylogenetic difference between the two Lichina species and all the other lichens studied (lines 89-95). One can argue that to more specifically elucidate the relative importance of habitat factors versus possible phylogenetic influence the two marine lichens should preferably have been compared with some inland species of Lichinaceae (Lichinales) and not with species representing other orders of Ascomycota?

Also the possible influence of thallus morphology (surface/volume ratios, gelatinous thalli versus air-filled medulla, etc.) could be touched upon - but as said, one cannot discuss everything in one paper.

Line 274 		Replace period before ”inland lichens” with comma.
Line 316		This is in contrast to the…
Lines 369-372		Consider rephrasing this text (maybe by splitting into several sentences).


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: MARINE CYANOLICHENS FROM DIFFERENT LITTORAL ZONES ARE ASSOCIATED WITH DISTINCT BACTERIAL COMMUNITIES
Review round: 1
Reviewer: 3

Output:
Basic reporting: This article is very well written. The authors did a great job in clearly articulating the goals of the study. They also were thoughtful when referencing the literature.

Regarding the organization of the text, it would be helpful if the authors listed their questions on page 5 lines 123-128 in the same order that the questions were answered.

Regarding figure 2, the color choice makes it difficult to distinguish between the samples. For example, both on the screen and on paper, it was difficult to separate L confinis from L. Lichenoids. Likewise L. pygmaea and seawater were hard to separate by color.

Page 15, First paragraph. Please include information about the symbiont of Xanthoria.
Experimental design: The question of marine lichens microbiome is well defined and very interesting. It has not been addressed before this study and is relevant both from an ecological point of view as well as the potential for bioprospecting.  The methods were well described.

The authors are very careful and have gone so far as to include a mock community in the sequence analysis. They candidly reported that the mock community showed some contamination (~0.5%). To account for contamination, the authors removed sequences with low variance across their samples. While ideally they would resequence their samples, this treatment is acceptable. However, the authors should mention somewhere in the text that it could introduce a bias, particularly with low abundance sequences since not all sequences are amplified equally during the sequencing reactions.

Minor comments:
1)	Page 6 line 135. It would be helpful to cite in the text the how far apart the clusters are from each other (it is currently in the supplementary material) but from reading the text it is hard to know if they were miles or meters apart. It would also be helpful to clarify the distances in page 18 line 527 when the authors say there was no effect across horizontal distances.
2)	Page 6 Line 143. Please indicate what part of the lichen was sampled
Validity of the findings: Overall, the conclusions are supported by the data.

My only concern is the comparison of the cultured samples to the culture independent results. Ideally the cultured samples would have been freshly cultured from the same lichen isolates used for the culture-independent study but I realize that is not possible at this point.  Were the cultured samples taken from the same site? The data in the paper shows, at least with Xanthoria, the location affects the composition. The description of these results should be expanded. Did the host species correlate in the samples?

Overall the discussion was excellent. The most interesting point was the comparison of terrestrial versus marine lichens. This could have been put earlier to emphasize it more. (it was somewhat buried in the discussion).

Minor comments:
1.	Page 14 Line 418-420, was the difference between the different Xanthoria samples calculated by DESeq2 or by the OTUS specific for each location?

2.	Page 21 lines 635 to 651. The last paragraph of the discussion is very speculative. While it is within the guidelines of the journal to include some speculation in the discussion, it is a bit distracting and could be shortened.
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: MARINE CYANOLICHENS FROM DIFFERENT LITTORAL ZONES ARE ASSOCIATED WITH DISTINCT BACTERIAL COMMUNITIES
Review round: 2
Reviewer: 1

Output:
Basic reporting: This is a much better version of the manuscript. As all my comments have been taken into consideration, I think the paper is now suitable for publication. I would however recommend one more careful read to improve the writing of the text, especially in the newly-written parts. This would increase the quality of the paper and make it a nicer read.

A few suggestions:
In the abstract, microbiome has been replaced by microbiont in the first sentence. I’m not familiar with this term and it adds confusion. Microbial or microbiome would better fit.
Line 33: I would say “strictly marine”
Line 58: I think a word is missing, maybe “and”, before allows
Line 61: I don’t think you should say “also” as you haven’t given examples yet.
Line 64: I’d rather say “fit with” than “fit to”
Line 68: the reference shouldn’t be inside parentheses. Same for line 140.
Line 143 lead should be led
Line 148-150 you wrote characterised then characterized
Line 151: associated to should be associated with
Line 171 were should be was
Line 544 none this should be none of this
Experimental design: The experimental design is sound and my comments have been taken into consideration.
Validity of the findings: Findings are valid.
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: ILLUSORY RESIZING OF THE PAINFUL KNEE IS ANALGESIC IN SYMPTOMATIC KNEE OSTEOARTHRITIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript entitled with “Illusory re-sizing of the painful knee is analgesic in symptomatic knee osteoarthritis” by Stanton et al. is clearly structured and written in professional and unambiguous language. To my opinion, the main findings are sufficiently emphasized. The proof-of-concept study provides a novel treatment option based on a body part illusion employing multimodal integration with bodily signals. The augmented-reality application sounds promising and after a well-applicable and affordable method in everyday clinical practice. The authors found a significant pain reduction only using the multimodal visuotactile illusion. The authors found increased analgesia with repeated trials of the visuotactile illusion, however, the authors critically discuss that a potentially to low dosage was the reason for not observing sustained pain reduction in daily pain ratings. The cumulative analgesic effects are important for clinical practice.
However, there are certain aspects mainly concerning shortages in the methods description and the experimental design that shall be addressed by the authors.
Experimental design: A. First-person vs third-person perspective:
I suggest reporting on the additional factor of looking at the knee from a first-person perspective vs. a third-person perspective. The frame of reference (e.g., egocentric vs. allocentric) is a crucial factor determining the effectiveness of bodily illusions and the phenomenal experience of ownership (Blanke, 2012). The authors report that some subjects performed the conditions from a first-person perspective while the others performed the task from a third-person perspective in the method section. Potential differences between both viewpoints were not addresses later on. I suggest reporting on potential differences, since the authors also speculate that the sense of ownership might be an important mediator of the effectiveness of the VT illusion in the discussion part without showing data on ownership experiences during the conditions.

B. Baseline pain description in the methods section:
The authors report on daily pain assessments between session 2 and session 3 and that statistical comparison were performed between the baseline pain and the pain directly after session to and prior to session 3. However, from the methods section it is not obvious to me when the baseline pain measurement was assessed and whether it was also assessed outside of the laboratory environment and thus similar to the pain diary assessments. The first description of the baseline is given in the results section in Line 206 as far as I can see.

C. No ratings on the strength and vividness of the VT illusion and pain descriptives
The authors discuss (speculate) that sense of ownership might be an important aspect of the treatment efficacy. However, the authors do not show results demonstrating the intensity of the illusion and whether it was linked to the analgesic effect.

D. Rigid-body vs. non-rigid body transformation of visualized body parts:
The motivation of using stretching and shrinking visuotactile illusions rather than magnifying and minimizing illusions could be emphasized and contrasted more. The authors compare on pain modulation via shrinking/stretching, while former literature (also referenced by the authors) refer to magnifying and minimizing illusions. While the former describes affine (rigid-body) transformations in shown body parts the latter refers to non-affine alterations in visualized body sizes. The article on shrinking vs stretching illusions (Gilpin et al., 2015) only looked at the presence of malformed hand representation in hand OA but not on illusion-related alterations in pain.

E. Further points:
I was unable to find the total duration of session 1 as well as the duration of the eight individual conditions.

It was not obvious to me if the subjects were able to see the other leg. Was the other leg visually occluded? I suggest addressing these points in the methods section.

The authors commonly refer to illusion conditions, however the VO, TO and incongruent VT are expected to not elicit illusory precepts. I suggest substituting ‘illusion’ by ‘condition’ if necessary.

I suggest rephrasing pre-/post-illusion pain scores to pre-/post-condition pain scores since the control conditions do not elicit an illusory percept.
Validity of the findings: The authors do not report on whether the assumptions to perform repeated measures ANOVAs were fulfilled (e.g., test of sphericity, normality…).

Due to high drop-out rates in session 2 and session 3 linear mixed models might be a fruitful alternative to repeated measures ANOVA due to their ability to deal with outliers fairly well.

The authors do not clearly state that they performed a priori contrasts in the methods section (e.g., Line 145) but report on planned contrasts in the Figure description 2. Thus, I strongly recommend explicitly mentioning in which cases planned contrast or otherwise multiple comparisons control were performed in the methods section.

The authors report that sometimes the shrinking and sometimes the stretching congruent VT illusion was most analgesic. It would be interesting to know whether the verbal description of pain is qualitatively related to the higher effectiveness of either the stretch or shrink illusion. For instance the McGill Pain Questionnaire assesses whether pain is perceived to be ‘pressing’ or ‘pulling’. Do the authors have data on how the patients describe their OA knee pain?

The authors conclude that multimodal integration and the generation of an illusory re-sizing of the knee is a key aspect of the immediate and prolonged pain reduction. But, the authors also report that the congruent and incongruent VT conditions were most effective at reducing pain. The incongruent VT illusion is, however, expected to not induce an illusory percept and not to be associated with strong multimodal integration due to spatiotemporal incongruence between visual and tactile input (Blanke et al., 2015). Moreover, some of the participants performed the VT conditions from a third person perspective, which might have lowered the sense of ownership additionally. Thus I am not fully convinced that multimodal integration and illusory re-sizing precepts are the key aspect of the therapeutic pain reduction found. Do the authors have data on the illusory strength in the incongruent VT condition to address that point?
Additional comments: Figures and Tables
Figure 2:
•	I recommend writing ‘A significant Condition x Time interaction was found’
•	I suggest reporting on the verbal endpoints of the 0-100 NRS
•	I recommend an indication of what the error bars represent (M ± CI, SE or SD).
Figure 3:
•	I recommend rephrasing the title to […] over ten repeated illusion trials.
•	I recommend rephrasing to […] between the first and tenth illusion trial, […]
•	I suggest reporting on the verbal endpoints of the 0-100 NRS
•	I recommend an indication of what the error bars represent (M ± CI, SE or SD).
Table 1:
•	I recommend indicating verbal endpoints of scales if existing
Abstract
Line 28-29: I suggest speaking about body representations rather than brain-based body representations since (1) no brain imaging was performed and (2) mental as well as neural body representations support a link to pain.
Line 34: I suggest highlighting the verbal endpoints of the 0-100 numerical ratings scale.
Introduction
Line 61-62: Please add references.
Line 63: I suggest introducing the terminology of ‘visually induced analgesia’ (Longo et al., 2009)
Lines 78-79: I recommend rephrasing to ‘the effect of only a single illusion intervention’ since one illusion might be confused with one type of illusion.
Line 88: I would prefer to read a short description of the diagnosis criteria on knee OA.
Materials and Methods:
Line 88: I recommend referring to participants or subjects rather than people.
Line 121: visual image elongate(s)/shrinks
Line 128:
a.	Since the control conditions did not induce an illusion, I suggest rephrasing to ‘[…] was evaluated before and after each condition.’
b.	Rephrase: between each test condition  confusing since most conditions served as control conditions.
Line 133-134: ‘was evaluated again’ rather ‘was again evaluated’.
Line 147: the abbreviation ‘RM ANOVA’ was not introduced beforehand. In line 145 repeated measures ANOVA is used.
Line 157: change 1st to 1st.
Results
Line 163: I suggest reporting on the ACR criteria shortly. Abbreviation ACR not introduced here or in the methods section.
Line 241: the abbreviation S1 was not introduced.
Line 250: the abbreviation PPC was not introduced.
Line 316: Please add a reference: … past work (…).
Line 320: the abbreviation NRS was not introduced.
Line 403: Please change ‘..Pain’ to ‘.Pain’
Line 418: Please change ‘.. Eur J Pain’ to ‘. Eur J Pain’
Inconsistencies:
•	resize vs. re-size
•	VT illusion vs. VT illusions
•	p = XXX vs. p=XXX
•	I suggest spelling in full numbers between zero and twelve.

LITERATURE
Blanke O. Multisensory brain mechanisms of bodily self-consciousness. Nat. Rev. Neurosci. 2012; 13: 556–571.
Blanke O, Slater M, Serino A. Behavioral, Neural, and Computational Principles of Bodily Self-Consciousness. Neuron 2015; 88: 145–166.
Gilpin HR, Moseley GL, Stanton TR, Newport R. Evidence for distorted mental representation of the hand in osteoarthritis. Rheumatology (Oxford). 2015; 54: 678–82.
Longo MR, Betti V, Aglioti SM, Haggard P. Visually induced analgesia: seeing the body reduces pain. J. Neurosci. 2009; 29: 12125–12130.


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: ILLUSORY RESIZING OF THE PAINFUL KNEE IS ANALGESIC IN SYMPTOMATIC KNEE OSTEOARTHRITIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper is written very well, with sufficient references. Note that there has been some controversy regarding body illusions and analgesia - see
http://www.jpain.org/article/S1526-5900(17)30017-2/abstract
https://onlinelibrary.wiley.com/doi/full/10.1002/ejp.606

In the abstract the authors refer to "brain-based body representations". I don't understand the 'brain-based' part of this. Aren't all body representations 'brain-based'? I think that the 'brain-based' can be left out. Perhaps 'illusory body representations' might be preferable, since that is what is being dealt with.

The paper is self-contained, and follows the expected structure.
Experimental design: The research is certainly within the aims and scope of the journal, being an original study with a well-defined research question that provides new information about the field of research.

The work is carried out to a high standard.

The setup with respect to participants being seated or standing is not clear. I don't understand why if they would stand it would be equivalent to looking in a mirror. This wasn't clear from the video, which, I think only had the sitting down condition.
Validity of the findings: The analysis has been carried out satisfactorily. On line 94 the authors refer to an 'f' value. Presumably this is an effect size, but it needs to be specified which one. I think most researchers will know Cohen's d, but there are many others, and it isn't obvious what 'f' refers to.

Following the repeated measures ANOVA the authors use paired t-tests (e.g., line 145, 155, 173, ...). I think that these have not been controlled for multiple comparisons. There are very many tests in this paper, so some attention to the issue of multiple comparisons would be useful. I would avoid the Bonferroni which is extremely conservative. The authors might like to consider this approach, which is simple to do and has had more than 40,000 citations:
http://www.stat.purdue.edu/~doerge/BIOINFORM.D/FALL06/Benjamini%20and%20Y%20FDR.pdf
However, I'm not insisting on this, but the number of comparisons could be a problem.
Additional comments: This paper adds usefully to the literature, and apart from the minor points above is ready for publication.


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

Input:
Title: ILLUSORY RESIZING OF THE PAINFUL KNEE IS ANALGESIC IN SYMPTOMATIC KNEE OSTEOARTHRITIS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The concerns mentioned in my minor revision were fully met by the authors.
The shortages in the description of the illusion induction as well as the statistical analysis were met by the authors.
The manuscript reads very well.
Experimental design: The authors give a sufficient description of the experimental paradigm. Moreover, the shortages in the description of the statistical analysis (esp. regarding multiple comparisons control) were compensated.

Typo in Line 143: Greenhouse-Geissier --> Greenhouse-Geisser
Validity of the findings: The authors included a statistical comparison to detect potential differences between inducing the illusion from a third-persons versus first-person perspective, which helps understanding the mechanistic basis of the illusion.
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: ILLUSORY RESIZING OF THE PAINFUL KNEE IS ANALGESIC IN SYMPTOMATIC KNEE OSTEOARTHRITIS
Review round: 2
Reviewer: 2

Output:
Basic reporting: All comments have  been appropriately addressed.

I found this typo: lines 32-33
"recent work has highlighted that that differing effects likely relate to differences in methodology"
Experimental design: Previously discussed in first review.
Validity of the findings: Previously discussed in first review.
Additional comments: Previously discussed in first review.


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: METABOLISM IN A DEEP HYPERTROPHIC AQUATIC ECOSYSTEM WITH HIGH WATER-LEVEL FLUCTUATIONS: A DECADE OF RECORDS CONFIRMS SUSTAINED NET HETEROTROPHY
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1.Introduction

The importance of the work is clearly stated on the introduction. It is based on a lack of data and understanding the dynamics of tropical lakes and reservoirs towards a changing world. However, the introduction became too generic in addressing the objective of the research and left out important technical achievements in environmental data (i.e HFM data, hydrobiology…). I would suggest a deepening on this part. Quantity and quality of the references are good. Considering it is an introduction of a tropical study, the paper should give more emphasis to that (including the inclusion of previous works performed in such regions). Thermocline should be addressed.

2.Study Area

The description of the study area is incomplete for the understanding of a layperson. I suggest a better development on the climate description and overall information of the biological system. It is well known that the dynamics of the food web plays an important role on the primary production (see, Carpenter et al. studies in Lake Paul and Peter for instance).

3.Methods

The evaluation of the environmental variables is key for this work. However, the description of how data was granted is severely compromised by the lack of information. The selected methods are biased, but well accepted when other technologies are not available. Nevertheless, in this case, a development paragraph on the limitations of the methodology would be necessary

4.Figures

Please review the figure axis and especially the legends. They must be auto-explained. Figures are non-comprehensives.

5.Results

Results are too fragmented and there is no previous introduction of the analysis that would be done. The work lost its focus and the results became scattered, without a clear research question to be answered. The title suggests that the research question would be: how does a hypertrophic lake behave in face of high-level fluctuation? The way in which the paper was written does not help in logically addressing this question. I would suggest a dramatic re-structuration of the paper based on the clear and precise understanding of the research question. The content is plural and the data can be valuable if well explored.

There was a weak association between what is stated in the text and what is shown on the figures. This applies either for textual expression of the results as extraction of results from the data.

6.Discussion

The discussion is shallow, long, fragmented and brings to the table neither good references, comparative works, discussion of the data in face of other studies and so on. When the work loses the track on the middle it often ends like this. It is not that the information has no value. It just does not hit the point.
Experimental design: Experimental design is impossible to be evaluated due to the lack of information on how data was granted. The manuscript does not stand by itself.

The research area seemed to be well defined in the beginning of the manuscript but missed the track over it. So forth, failed to identify the knowledge gap and work the results towards it. Simply stating that such study is needed in a certain area does not fulfill the expectations of a scientific manuscript.
Validity of the findings: Results are too fragmented and there is no previous introduction of the analysis that would be done. The work lost its focus and the results became scattered, without a clear research question to be answered. The title suggests that the research question would be: how does a hypertrophic lake behave in face of high-level fluctuation? The way in which the paper was written does not help in logically addressing this question. I would suggest a dramatic re-structuration of the paper based on the clear and precise understanding of the research question. The content is plural and the data can be valuable if well explored.

There was a weak association between what is stated in the text and what is shown on the figures. This applies either for textual expression of the results as extraction of results from the data.
Additional comments: Please, have a deeper look on the paper. It has points that are unacceptable. The overall value and research were alright but there are many points of the manuscript that do not agree within itself. The study itself is important and such research shall always be motivated. Unfortunately, at this time the manuscript needs major revision.

The reviewer hereby states its lack of relevance regarding towards background of the researchers involved on this manuscript. The evaluation of the manuscript was based only and exclusively on the quality of the information and writing content, fully disregarding any consideration related to the country of origin, Institute of research or international prestige of the responsible Principal Investigator.


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: METABOLISM IN A DEEP HYPERTROPHIC AQUATIC ECOSYSTEM WITH HIGH WATER-LEVEL FLUCTUATIONS: A DECADE OF RECORDS CONFIRMS SUSTAINED NET HETEROTROPHY
Review round: 1
Reviewer: 2

Output:
Basic reporting: See my general comments.
Experimental design: See my general comments.
Validity of the findings: See my general comments.
Additional comments: This is an interesting study on long-term aquatic metabolism in a subtropical environment. Since there are too few instances of such studies worldwide, it is advisable to publish it. However, there are some hints and topics to be considered by authors before acceptance. They assume that metabolism of Valle del Bravo reservoir is not affected by chemical constraints due to its hypertrophic nature, but they do not offer any proof about. Instead, they make their analysis of controlling factors rely on purely physical features, the most important of which is fluctuating water level, with water temperature and transparency as other, lower significant factors. A proof that all these are not the one and only explanation of metabolic dynamics is that they do not amount to 100% of explained variability of GPP, NPP or Respiration (Lines 272-289). Therefore, they must search for other factors explaining the remaining variability, and the obvious candidates would be climate, the chemical environment and the herbivore plankton. Regrettably, nothing is said about. This undermines a study that is otherwise very interesting and would be welcome by aquatic ecologists worldwide if properly addressing controlling factors of long-term metabolism.
My recommendation is to accept this manuscript for publication, providing that authors thoroughly address this point. Other minor queries and suggestions are the following:
1st) Lines 62-64. “Furthermore, recent studies…”, please give more references in addition to that of Almeida et al. (2016).
2nd) Some information is missing from the Study area section. For example, the size of catchment area of BV reservoir, plankton composition in the long-term, organic carbon, chlorophyll-a and nutrient data and so on.
3rd) Oxygen undersaturation is reported during mixing for the whole water column. This is a bit surprising. It could reflect that sedimentary organic matter is so high that results in excess oxygen consumption that exceeds net oxygen production by phytoplankton throughout that period. Therefore, some supplementary data on sedimentary organic carbon, nitrogen and phosphorus might aid the reader to understand why this is so.
4th) Novel methodologies also have drawbacks and free-oxygen monitoring is not an exception. I agree with authors’ reluctance for not using it since strong winds make reaeration coefficient estimation unreliable. But the bottle incubation technique for measuring planktonic GPP and R has also limitations and these have been reported many times. Authors must be aware of them and provide a reference citation about.
5th) It is unclear the rationale behind the export capacity of organic matter from biomass settling (Lines 177-178). Please provide a reference and explain it more thoroughly.
6th) Some statistical testing seems advisable in some sentences when making comparisons (“higher than…”, “lower than…”). An example of this neglect can be found in Line 275. Also, the statistical significance of the GPP:R long-term trend is not ascertained (Line 300, Fig. 6), and the rate of increase differs between what is written in the text and the equation shown in the figure.
7th) Lines 317-318. It is doubtful that metabolic rates experience minor variations in time if one takes a look at Fig. 5 and Lines 2-58-268.
8th) The discussion section is a bit cumbersome and could be certainly shortened. For example, there are some obvious explanations that could be deleted, such as the ones in Lines 318-328.
9th) Since data on chlorophyll-a and dissolved organic carbon are lacking, authors fail to make their point stronger when dealing with the vagaries of and GPP limitation by the underwater light climate in Lines 330-337. If you have some data on those variables, you could try to envisage how much GPP variability is explained by such a climate (see Kirk’s book “Light and photosynthesis in aquatic environments”).
10th) Line 364. “Intensity of the winter”. What is it? Please explain it to a non-Mexican audience.
11th) Metabolism data in subtropical and tropical environments are much lower than those in temperate areas. Hence, it is good news to refer to this fact (Lines 433-442). And it would be even better if authors could add a table with most of them (they are not many!), also reporting older studies, for which bottle incubations were used, such as those by William Lewis, John Melack, Jean Pierre Carmouze, Mary Burgis et al. in African and South American lakes in the seventies.
12th) Literature references must be checked. Pages are missing in some instances.
13th) Figure 1 is interesting but the reader would gain more insight if wind- and upper mixed layer plots were added.
14th) Authors have used oxygen isoline as an index of mixed layer (Fig. 3). This is somewhat misleading. They do not always match. I suggest to reconsider such calculations and figure.
15th) Figure 4 is unuseful because it is of minor value within the long-term context addressed in the study.
16th) Tables 1-3. The variability-oriented reader will miss standard deviations for all variables reported.
17th) Please report variables represented by capital letters in Table 3. It is annoying to search for them in the main text when looking at the Table.


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: IS AUTUMN THE KEY FOR DENGUE EPIDEMICS IN NON ENDEMIC REGIONS? THE CASE OF ARGENTINA
Review round: 1
Reviewer: 1

Output:
Basic reporting: Generally, this manuscript was presented in well written English. But in many places, compound sentences with attributive clauses are ambiguous, better to be checked for syntactical corrections. The following are some examples:
   Line 30-32:  syntactical error
   Line 49-51: please reconstruct this sentence.
   Line 80-82: confusing sentence
   Line 98-100: syntactical error
   Line 174-176: syntactical error
   Line 231: in → of

Literature references were sufficiently presented and article structure was organized clearly. About supplementary materials, it would be more informative for readers if the case data are included in the supplementary part. And in currently existing supplementary txt, necessary explanation for abbreviations should be given as some are not shown in the Table 1.
Experimental design: This study is trying to explore the environmental factors that drive epidemic events in Argentina by employing well collected meteorological data from country-wide stations and annual dengue cases registered in SNVS. Good models can help forecast future epidemic outbreak. This topic is important in the field of epidemic, and author’s attempt is appreciable. This article involved no ethical issue, and conformed to PeerJ scope completely.

Technically, this article is a continuation of one published paper as referenced [Carbajo, Cardo & Vezzani, 2012]. Strict statistical analysis was conducted aiming to obtain optimum models which are capable of describing most contributive factors for dengue cases. Some details in the Materials & Methods need to be clarified.

    Line 134-137: Using climatic data from 15 meteorological stations, interpolation for the whole country was conducted based on 15 km square cell grid. The sensitivity analysis of models to meteorological station data is necessary, considering the accuracy and reliability of sparse data including eight artificial stations.

   Line 142: While definition of DPT was oriented in reference (Carbajo, Cardo & Vezzani, 2012), explicit presentation of DNT, i.e., mathematical relationship between DNT and temperature variable is essential in this article. Because following results regarding DNT and DPT were showed alternatively, comparative differences between the two terms need to be illustrated.
Validity of the findings: Selected models according to three approaches are of high power to explain response variable, i.e., dengue cases. Following points are expected to complete model analysis.

1) Considering final results were presented with selected mathematical models according to three statistical approaches, more explicit comparisons among candidate models should be given. For instance, in Line 342-343, authors summarize no association with El Niño, but in prior part, there are no analysis involving El Niño events as explanatory variable.
2) Line 305: 2009 epidemic model was rerun for 2016 epidemic, but showing low predictive power. The only explanation that different source countries of infection is not enough, which cannot manifest the epidemic nature.
Additional comments: Authors did a good job to identify environment factor closely related with dengue cases. Statistical approached were well designed and brief results were presented. However, in order to make this article more readable,  written English is better to be 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: IS AUTUMN THE KEY FOR DENGUE EPIDEMICS IN NON ENDEMIC REGIONS? THE CASE OF ARGENTINA
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall well written with few minor wording errors

Raw data have been shared.

Introduction:
L56 Briefly describe the clinical presentation of dengue virus infections.
L59 Note that the large increase in dengue cases in 2015 was due in large part to the CHIKV epidemic. Many CHIKV cases were misdiagnosed as DENV. I suggest picking a different time period for comparison.
L67 How many cases of ZIKV in Argentina? Imported or locally acquired?
L69 Correction: "an outbreak of YF was reported in the Amazon basin in 2017 with [number] of cases."
L79 Describe how/why climate affects arbovirus transmission and include relevant references from lab and field studies. Provide relevant background on the behavior of the mosquito vector.
L80 Describe what is meant by the  "close association"
L82. Climate variability at what time scale? Seasonal, interannual, decadal, etc.
L85 El Niño and La Niña events have also been associated with dengue and malaria transmission in Latin America (please cite relevant literature).
L90. Update the reference: Carbajo et al in press.

Figures/Tables:
Table 2: Instead of a table, you could show a bar graph with a series of the annual cases and use different symbology in the bars to show the different categories of transmission intensity.
Table 3: For each model, please show parameter estimates, SE, p values
Figure 1. Please clarify in the figure legend how the sites were selected where the squares are located. What does "other" refer to? Please provide more detail in the figure legend.

The discussion lacks a robust interpretation of the results in comparison to the findings from other relevant studies, other than those by the authors. Please add references.
Experimental design: Major comments:
L 123 Did you analyze how the independent variables are correlated? It would be helpful to see a correlation matrix as supplementary information.
L132 Explain why these dependent variables were selected (e.g., distance to the nearest water body and % of population change). Did you examine maximum temperature and relative humidity?
L134 What is meant by the following “average records from the period July 2011- June 2016 were used to smooth distinctive and/or anomalous features of the year before and during the epidemic.” What smoothing function was used? Normally you calculate anomalies using the entire climatological time series (ideally +10 years), rather than 1 year before or after.
L144 Although the model was described previously (Carbajo et al 2012) please provide basic information about the mathematical model, including formulas and parameters. This is an important component of this paper and should be well understood. How has the model been updated/advanced since the last publication?  Does the model consider the nonlinear response of the mosquito vector and viral replication in relation to temperature? See recent work by Mordecai et al 2017 PLOS NTD and other authors. Consider showing how the DNT and DPT vary with temperature.
L154 Please define El Niño events and the Niño 4. Why was this value used instead of the Niño3.4, which is more commonly used and forecasted?
L157 Why would you sum the Niño monthly index? I don't understand these variables. Also, you use the annual time period (Jan-Dec), whereas in the analysis you define the annual time period as July-June. Please be consistent.
L165 By using dengue cases from the neighboring countries from the normal calendar year (Jan-Dec), this automatically introduces a temporal lag into the analysis, since the normal calendar year begins 6 months before the beginning of the year in the analysis (July).
L202 Did you test any temporal lags of the dependent variables with respect to dengue counts?
L211, 216 (and elsewhere in the paper). The models developed here are not forecast models. If you are forecasting (predicting dengue transmission in future time periods), please describe the methods. Are you leaving out years in the time series and predicting those years using the rest of the time series? Are you using seasonal climate forecasts? etc. If yes, show time series with the forecast results.
L 213, L224, L267 Number of disease cases should be divided by population to capture disease incidence (e.g., 100 cases per 10,000 people). By not correcting for population, human population becomes a predictor in the model, which is self evident (we have more cases where we have more people in areas suitable for transmission) (L292)
L213 How were these 4 categories for transmission intensity selected? I suggest using quartiles (25/50/75th %) for the categories.
L267 Why was this threshold selected?

Minor comments:
L104. Please briefly describe the climatology of the study area. What are the key macro-climatic drivers of interannual variability in rainfall and temperature? (e.g., ENSO events or other phenomena)
L105. What diagnostic tests are used to confirm the cases by laboratory surveillance?
L 125 Please provide more information about the specific climate product used in this analysis. I could not find this information on the website provided.
L130 What data were used to confirm that the vector was present in the district? Please include this information.
L130 How were the 3 regions delimited/identified?
L237 In the methods, please describe the source of the demographic data and the datasets that were used.
L256. The authors indicate that they deliberately excluded variables with no forecasting power in the model. Which variables were included and why?
L304. In order to estimate annual population, you could use a linear extrapolation between census years, allowing you to project population based on prior trends in population growth.
Validity of the findings: The model and data sources require more description in order to understand and assess the validity of the results of the analysis.
Additional comments: The authors present a spatial and temporal analysis of dengue transmission in Argentina in relation to climate conditions and transmission in neighboring countries. The most important contribute of the paper is the identification of the autumn season as a key period regulating dengue transmission and the importance of dengue transmission in neighboring endemic countries. Although the paper addresses an important topic, it is not publishable in its current form. Specific recommendations are identified above.


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: IS AUTUMN THE KEY FOR DENGUE EPIDEMICS IN NON ENDEMIC REGIONS? THE CASE OF ARGENTINA
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Authors have addressed all my comments. Necessary information had been added; there are no further comments on 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: IS AUTUMN THE KEY FOR DENGUE EPIDEMICS IN NON ENDEMIC REGIONS? THE CASE OF ARGENTINA
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The authors have done a great job with the revisions. I have no further 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: WATERBIRD COUNTS ON LARGE WATER BODIES: COMPARING GROUND AND AERIAL METHODS DURING DIFFERENT ICE CONDITIONS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Basic reporting is solid.
Experimental design: Experimental design is solid, but analysis methods require more clarification and justification as detailed in general comments.
Validity of the findings: Validity is reasonable, but analysis methods require more clarification and justification as detailed in general comments.
Additional comments: General comments

line 108: Was the statistical replicate the ten different sampling occasions, multiplied by the two methods, multiplied by the number of species?

line 113: Were the counts from several observers for each count method and sampling occasion summed before analysis?

line 113, 276: Are you certain that the higher counts are more accurate that the lower counts?  Is either method more likely to have double counting?

line 117: Were all the counters good? Were they randomly assigned to methods and ice conditions?

line 150: Why was the interaction between ice and method coded as a random effect, as described in the statistics section?  There would only be four combinations of ice and method to estimate slope variance.  Seems like it would be better to treat this as fixed:

count ~ global intercept + random species intercept + ice + method + (ice x method)

This model could easily produce the output found in table 1 and figure 2D. Looking at table S2 it looks like you treated the interaction as fixed, after all, as it is found in an F-table.  What's up with that?

Also, keep in mind that the models described so far assume the same slopes per species. However, you spend a few paragraphs and figure panels describing variation among species (line 168-190, 231-263).  If variation among species was indeed important, why not have fixed species terms in your model? For example:

count ~ global intercept + ice + method + species group + (ice x method) + (ice x species group) + (method x species group) + (ice x method x species group).

That is the model implied by figures 2A-C, and would allow you to better interpret the importance of the different colored slopes.  It isn't critical that you do this, but it makes the species variation discussion more believable.

line 151: The log-link function is the standard for Negative Binomial regression. Why the identity link in your study? Were the count data really normally distributed?

line 151: For the ice variable, you jump from 0% ice (0) to > 70% ice (1)?  Is this correct? What about in-between values? Didn't exist in your study?

line 152: The Arkusz2 and Arkusz3 tabs are empty on you XLSX data sheet.

line 155: How did you estimate standard errors and confidence intervals found in various tables? From model output? Simple summary statistics?


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: WATERBIRD COUNTS ON LARGE WATER BODIES: COMPARING GROUND AND AERIAL METHODS DURING DIFFERENT ICE CONDITIONS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper meets all basic reporting requirements.
Experimental design: The paper needs improvement in the description of methods, as noted below:

- Please add a section to the methods describing methodology for cost accounting.
- Please add a statement to the methods acknowledging that because the two count methods could not be compared to a completely unbiased estimator, but instead could only be compared to each other, the method giving higher total counts was considered to be the superior (if this is true).
- Please explain in the introduction or methods why you grouped the species detected into the groups that you used (i.e., different panels in fig 2). Are the different groups of different conservation concern, or expected to exhibit different detectability with regard to ice and observation method?  Why not simply group all species together?
Validity of the findings: The paper requires improvement in discussion of the findings, as noted below:

- The manuscript relies on an unchallenged assumption that the survey method that gives higher counts is the superior method. The manuscript would benefit from a more full discussion of potential sources of bias in both aerial and ground survey methods, or at the least an acknowledgment of the assumption that higher counts is assumed to indicate a superior method.
- I am not convinced that the main conclusions drawn by the authors are supported by the analysis in the paper. The authors conclude in line 211 that the major factor influencing census results was ice cover. However, figure 2 shows major differences between the two survey methods (ground vs aerial) regardless of ice presence, for some species.  I suggest that the authors should either revise their analysis to focus on broader patterns (for example, include species as a random effect in an overall analysis of count ~ census method + ice condition + census method * ice interaction), or be more conservative in their conclusions (for example, acknowledge that the detection of some species is more strongly affected by ice cover than others).
- Figure 2 needs improvement. I suggest plotting points rather than lines, identifying species or groups by point shape or color.  I suggest adding confidence intervals.  I suggest grouping species into biologically meaningful categories and displaying the means of each group rather than displaying each species individually, leaving the individual species means to be communicated in the S1 table.
Additional comments: Small suggested changes are noted below:

- Please clarify the meaning of "overall result" in lines 87-88: does this refer to "number of birds detected"?
- Please clarify the meaning of "ice conditions" in line 90: suggest rewording to "conditions when ice is present"
- Figure 1: please darken the country borders in the overview, small inset map, to make them easier to see. In addition, please add more information to the caption for example explain that Szczecin and Police are towns. Please explain the difference between observation points and transects in the figure caption.
- Line 153 and throughout: please be consistent with terminology, using only one of "count type", "method", "platform" throughout manuscript
- LIne 168: please explain why the species in fig 2 were separated into the various panels, referring if necessary to the fuller explanation that should be added to introduction or methods.
- Lines 205-209: this paragraph is interpretation and belongs in the discussion.
- Throughout: please use scientific names only, the mixing of scientific and common names is confusing for a non-expert.


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: WATERBIRD COUNTS ON LARGE WATER BODIES: COMPARING GROUND AND AERIAL METHODS DURING DIFFERENT ICE CONDITIONS
Review round: 1
Reviewer: 3

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: At present, I am not convinced that the analysis correctly accounts for the paired nature of the counts (i.e. ground- and aerial-based counts were done on the same day and should return the same number of waterfowl). By pooling all counts for each method into a single estimate, the analysis potentially overlooks differences observed within individual count dates. Adding count date as a random effect in your models might be one way to account for this. Alternatively, calculating the difference between the two counts on each particular date and then running a t-test to determine whether the difference changes between ice-free and ice conditions would be another way to account for this.

These surveys relate to only a single waterbody. Although likely to be generalizable to other locations, there is little in the way of discussion about this potential limitation of the study.
Additional comments: This manuscript represents research that will likely to be of interest to many biologists monitoring waterfowl at higher latitudes. It seeks to identify differences in the numbers of waterfowl recorded during aerial- and ground-based counts conducted of the same study area under different ice conditions. They find that although ground-based counts generally return higher counts of waterfowl in the absence of ice, aerial counts produce higher counts when the waterbody has high ice coverage. The authors identify species-specific differences from these general patterns, suggesting which species are most suitable for counting using the two methods. They also provide costings for the two methods, giving readers an understanding of how cost-effective each method may be under various scenarios.
The manuscript was very clearly written and clearly presents the work and their findings. I believe that the authors have adequately grounded their research in the literature on this topic and found that the introduction was well composed. Aside from some minor comments, mostly related to softening how definitive the authors are in the interpretation of their results, I believe that this manuscript will make a worthwhile contribution to the field.
General comments
•	Throughout the manuscript, accuracy is implicitly assumed to coincide with the count that returns the highest number of individuals. No discussion is made of the potential for double counting of some individuals to inflate the number of waterfowl recorded. If double counting is particularly high for one method in general, or during certain ice conditions, then there is the potential that the results do not conform to the interpretation of the authors. At the very least, some discussion of the likelihood of double counting for each technique needs to be made. For instance, it would be good to know whether waterfowl remained on the water surface following overflight of the survey aircraft, or if they flushed to a neighbouring area where they could have potentially been counted again on a successive pass. Similarly, how did the ground counters monitor bird movements when they were walking between successive count stations?
•	The authors state definitively that the two methods can be used interchangeably during ice-free conditions because the magnitude of the difference between counts of the two methods is small. However, their results indicate that the total difference is approximately 10%. If a monitoring program is intending to document population change, 10% noise in the data would drastically reduce statistical power to detect a population decline (or increase). At the very least, no decline smaller than 10% could be detected with any confidence without a correction factor being introduced. I would very much like to see the authors rephrase their assertion to something like ‘the observed difference (~10%) between methods may be acceptable in some situations for the two methods to be used interchangeably. However, researchers must consider the influence these small difference between methods might have on their results and consider developing correction factors where these differences are deemed unacceptable.’
Specific comments
L151-152 The ‘1 – over 70%’ presentation makes it confusing as to whether you were categorising 1% ice cover to more than 70% ice cover as ice conditions. I suggest using ‘1. Over 70% of surface covered by ice’ instead of the dash.
L173 ‘greater efficiency of species identification using this method.’ Could it not be that other species are mis-identified as this species rather than you are better at identifying it from the air. Seems unlikely that an observer travelling at 100 km/h could identify it more easily than someone with a scope.
L189 To state that the species are similar in their behaviour seems to be an oversimplification here. Maybe you could state that they are similar in their foraging method (for which there are studies that could be cited) because there is potential that behavioural differences are still responsible for this observation? For instance they may show different responses (flush vs dive) to overflight of the survey aircraft. Clearly there is something different about their appearance or behaviour that is driving these disparities and to pose that they are similar in their behaviour, I believe, is a misrepresentation.
L197 Please insert ‘ground’ in front of ‘counting’ to make it clear that you are reimbursing only the ground counters not those in the aircraft.
L199-201 I am not sure that it is accurate to state that the cost of the aerial survey is 212 € per 100 km of coastline because the survey plane would not have to make transect flights out over the waterbody. Therefore, total flight time would be reduced if biologists were interested in only counting a linear strip along a coastline.
L206 ‘Methodologically justified technique’ Please explain what you mean by this. Are you claiming that they are more repeatable, are more accurate, are safer (which they are not)?
L208 ‘Only one disadvantage of an aerial count’ Wrong. I can think of many. They are more dangerous (http://profile.iiaa.org/sites/default/files/images/Obits/Sasse-2000-WSB.pdf), surveys may need to be conducted in places where there are airspace restrictions, difficulties in identifying taxa with similar appearance, high levels of disturbance to the wildlife in some situations. These points need to be briefly mentioned in the discussion.
L212 ‘ground counts gave better results than aerial ones.’ You do not know this for certain. You have based your assessment of accuracy on size of the count. As you do not know the true number of individuals in the population, you cannot state that they are better. You can say ‘ground counts gave higher numbers relative to aerial ones.’ As per my general comment, any reference to the accuracy of the count needs to be removed from the discussion.
L216-217 ‘does not really matter which censusing method is used during ice-free conditions as the counts are not specially affected by this.’ This statement is far too flippant. See my general comments as to why a 10% difference is likely unacceptable in many situations.
L232 ‘real number of birds’ you cannot claim to know the real number.
L224 ‘underestimated’ again, you do not know this. Both counts could have overestimated the true number if double counting was substantial in both methods.
L226-227 comparing the results here to inaccessible lakes seems unjustified. It is not until the next paragraph that the reader gets a sense that under ice conditions patches of open water are inaccessible to the ground counters. Your methods state that the survey was designed to effectively cover the entire survey area, so the reader is led to believe that no areas are inaccessible. You may need to introduce the concept that some areas of the waterbody are indeed inaccessible to ground counters prior to discussing the similarities of your study with those where accessibility has previously proved difficult.
L263 ‘underestimate’ replace with ‘low relative to ground counts’.
Figure 2. I would like to see error bars on plots a-c
Figure 2. The numbers reported in plots a and b exceed the total number of birds reported in plot d (and table 1). I suspect this is an error due to a missing decimal point?


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: WATERBIRD COUNTS ON LARGE WATER BODIES: COMPARING GROUND AND AERIAL METHODS DURING DIFFERENT ICE CONDITIONS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The paper meets all basic reporting requirements.
Experimental design: The experimental design is sound.
Validity of the findings: The analysis and presentation of findings are strong.
Additional comments: Thank you for your extensive revisions, I believe the paper is much stronger following your revisions.  I wish you the best!


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: CRITERION-RELATED VALIDITY AND RELIABILITY OF THE URDU VERSION OF THE PATIENT HEALTH QUESTIONNAIRE IN A SAMPLE OF COMMUNITY-BASED PREGNANT WOMEN IN PAKISTAN
Review round: 1
Reviewer: 1

Output:
Basic reporting: This is a generally well-conducted study that usefully extends knowledge concerning the psychometric characteristics of an accessible and well-used measure. The findings are based on a large sample and will enable researchers to use the PHQ-9 with Urdu-speakers with greater confidence and clarity.

Some relatively minor corrections to the reporting would assist accuracy, clarity and readability; although most aspects of the design, conduct and analysis appear adequate, there are some key study limitations that need to be highlighted, and the overall reporting must better consider the context of depression screening/ case finding. The paper would benefit from the authors' checking the STARD guidelines (e.g. http://bmjopen.bmj.com/content/6/11/e012799) and considering relevant areas for further detail.

In the introduction section, the authors rightly quantify the impact of depressive disorder, making appropriate use of most recent Global Burden of Disease findings.
I find the initial sentences a little confusing and unnecessary- and would recommend omitting the first clauses (‘’It was listed as the fourth-leading cause of global disability adjusted life years (DALYs) in 1990, and was projected to become the second-leading 57 cause by 2020 (Murray et al. 1996). Reanalysis of the Global Burden of Disease Study using more and updated data reduced this number, but still..).
I think that simply reporting current DAY rank is more appropriate – and maybe simply noting that the age adjusted ranking by DALY in 1990 1005 and 2015 has increased (from 19 to 15) -  I would omit the % global increase in DALY details that you have provided. (http://www.thelancet.com/pdfs/journals/lancet/PIIS0140-6736(16)31460-X.pdf  - Figure 2)
Rather than the material relating to prior DALY summary ranking, it could be useful to note that depressive disorder accounts for substantial years of life lived with a disability (YLD) - 8.2% of global YLDs in 2010, making this condition the second leading cause of YLDs.(Ferrari et al, 2013  http://journals.plos.org/plosmedicine/article?id=10.1371/journal.pmed.1001547).

In some places the supposed benefits and value of ‘depression screening’ appears over-emphasised. There is overlap and some shared usage for the terms screening and case-finding -  however, the available evidence does not seem to indicate clear benefits/ clinical usefulness of screening for depression in unselected groups (see for instance Thombs, 2014 http://www.bmj.com/content/348/bmj.g1253?variant=full-text&hwshib2=authn%3A1521546726%3A20180319%253A1ab0944b-ed16-45ab-b338-ee9cddfd397e%3A0%3A0%3A0%3A4CXS4yD783sDTM15gKwsHQ%3D%3D – and you will be aware that Manea et al summarise the uncertainties about this in the introduction to their review).
So, I would recommend you modify some instances of the use of this term: the sentence  - ‘…Therefore, having a valid screening tool is imperative not only for detection but, if compared to a diagnostic criterion tool, for impact evaluation of psychosocial interventions in this population..’ should be altered – maybe to note that - having a valid screening or case-finding tool will be useful to assist case identification, particularly in at-risk groups or in those patients where depression is suspected..
And earlier, where you note – ‘…easy to administer, valid and reliable screening tools that can detect depression are needed for both clinical care and research in geographic areas with limited access to psychiatric professionals.  it might be better to slightly modify this to ‘..easy to administer, valid and reliable screening tools that can assist in detecting depression may be useful in clinical care as well as in research ..

Clearly you have ethical approval for the parent studies, and you have noted this in parentheses at the start of the study design section; it could be useful to note here (explicitly) that ethical approval has been provided.

The results section would be improved by omitting comparison with other findings (Previous studies performed in the same area as that of the current study have reported prevalence of depressive disorder during pregnancy to be around 23-26% (Rahman et al. 2004; Rahman et al. 2008) – best only to compare findings in the Discussion section.

The initial sentence of the Discussion section should provide a little more brief accurate detail about depression screening – not just that ‘..issues around screening and accurate diagnosis are still being debated..’ this context is of key importance to the study/ topic and merits a little more detail.

In the Discussion or Conclusion section, it might be useful to consider providing a demonstration of what the psychometric values mean – i.e. a sentence or so indicating that at cut-off x and with sensitivity/ specificity values x, in a population with depression prevalence x%, then x% of newly identified cases are true cases (and - it would be useful to consider presenting this with prevalence rates determined by diagnostic interview rather than the usually higher values evident from symptom self-reports, and with prevalence of the level you report possibly together with pooled estimate rates [such as http://ww1.cpa-apc.org/Publications/Archives/CJP/2004/february/waraich.pdf]).
Experimental design: In the methods section detailing participants -  it is noted that ‘...The details of the trials and the recruitment criterion..’ – I am sure that this should be criteria (not criterion) , and it would be useful if brief summary inclusion criteria were provided, with note that full details are available in the prior publications. Eligibility criteria are of particular importance in appraising the value of diagnostic accuracy studies (see STARD item 6).
Some of this (participants) material would fit better in a procedure or ?test methods section or with a ‘setting’ sub heading (but see journal format for guidance).

In the initial part of the ‘test methods’ section, you provide detail of translation of the PHQ-9 to Urdu, - but previously in the introduction section you note that the Urdu translation has been used in  research in Pakistan and cite the or more publications. It would be useful to consider and clarify the rationale for, and the extent of, the further translation work that has been undertaken- the current text indicates a forward backward procedure with expert panel and relatively large test sample. I am uncertain as to why this was necessary (consider and clarify whether and what were the inadequacies in the published Urdu translated version).
Validity of the findings: It would be useful to specify that your analysis was particularly focused on evaluating PHQ-9 at standard cut-points – the STARD guidelines note the importance of - Definition of and rationale for test positivity cut-offs or result categories of the reference standard, distinguishing prespecified from exploratory
(See Cohen et al, 2016 http://bmjopen.bmj.com/content/6/11/e012799 item 12)

You note in the Discussion section (and elsewhere) that the assessment procedure did not utilise any blinding or masking – the same individuals administered the reference standard as the index test, all within the same interview. This is a potential source of bias in the study and you should use this term (potential bias) when identifying this limitation.

Studies that evaluate the screening tests / diagnostic accuracy should ensure removal any people/ patients who already have a diagnosis of, or are receiving treatment, for depression. Because screening is designed to identify those patients who may have a condition, but are neither seeking treatment nor have had the target condition otherwise recognised, then including any patients who are already identified as cases will increased prevalence and severity of depression in the sample, and may inflate the reported sensitivity of the index test in relation to the reference standard. (See - Thombs et al, 2011 -  Risk of bias from inclusion of patients who already have diagnosis of or are undergoing treatment for depression in diagnostic accuracy studies of screening tools for depression: Systematic review. BMJ 343: d4825. doi:10.1136/bmj.d4825. PubMed: 21852353.).
Again – you need to note and discuss the sample and recruitment in relation to this potential source of bias.
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: CRITERION-RELATED VALIDITY AND RELIABILITY OF THE URDU VERSION OF THE PATIENT HEALTH QUESTIONNAIRE IN A SAMPLE OF COMMUNITY-BASED PREGNANT WOMEN IN PAKISTAN
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: In this study the authors aimed to validate the Urdu version of the PHQ for use in community settings. The measure is validated against the gold-standard SCID. The authors used data collected from pregnant women as part of a larger study.

The authors note that the Urdu version of the PHQ has been used in hospital and community settings, and has been validated in clinical settings. This raises the question of why the authors would expect different results in their sample. The requirement for a valid tool to assess perinatal depression makes sense. Given the sample, the authors might like to frame their introduction with this rationale in mind. In line with this – the sample is not simply a rural community-based sample, but a sample of pregnant women in their 3rd trimester. The entire manuscript could be re-framed to more accurately reflect the sample.

Were any adjustments made as a result of the pilot testing with 250 women? Were these same women included in the final sample?

Through the first half of the paper the authors claim they analyse both the screening and baseline samples separately. As they themselves note in the results section, this seems nonsensical given it is predominantly the same sample of women. I suggest they restrict their description to only the screening sample throughout the manuscript.

Did the authors have any a priori guidelines for what they would consider to be acceptable sensitivity and specificity? Without this, the decision to accept 10 as the cut-off seems to be either arbitrary, or simply a confirmation that the existing cut-off is acceptable (as opposed to optimal). If the study is better conceptualised as a confirmation of the existing cut-off the manuscript should be re-framed to better reflect this.


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: CRITERION-RELATED VALIDITY AND RELIABILITY OF THE URDU VERSION OF THE PATIENT HEALTH QUESTIONNAIRE IN A SAMPLE OF COMMUNITY-BASED PREGNANT WOMEN IN PAKISTAN
Review round: 2
Reviewer: 1

Output:
Basic reporting: I am pleased to note that this re-submitted paper provides a well-written report of a worthwhile study, which will be of interest and value to academic and clinical colleagues.
Experimental design: The amended report provides clear detail of the approach and methods, which appear appropriate and involve sufficient rigour.
The study deign and procedures appear to conform to STARD guidelines - my one additional suggestion is that you make explicit mention in the manuscript that you have followed STARD guidelines in the reporting of this study.
Validity of the findings: No further comments
Additional comments: Thanks for responding so clearly and comprehensively to the suggestions.


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: CRITERION-RELATED VALIDITY AND RELIABILITY OF THE URDU VERSION OF THE PATIENT HEALTH QUESTIONNAIRE IN A SAMPLE OF COMMUNITY-BASED PREGNANT WOMEN IN PAKISTAN
Review round: 2
Reviewer: 2

Output:
Basic reporting: Generally well-written.
Experimental design: The design is sound, but as currently presented the sample used does not match the research question. See comments below, and on previous review about suggested re-framing.
Validity of the findings: The validity of the findings is fine, but implications can only be applied to samples of pregnant women, not rural areas of LMICs.
Additional comments: The authors have made a number of recommended changes that improve the manuscript. However, while they do acknowledge that they specifically sampled a group of pregnant women, the entire manuscript as still framed as assessing depression in a community-based sample. I still believe a stronger emphasis on the need to assess depression in pregnant women specifically would strengthen the rationale for the study, which would then match the sample. Likewise, the results will not simply be "especially applicable to pregnant women"; they will only be applicable to pregnant women.  In my view this focus needs to come through in the manuscript title, the abstract and the manuscript itself. Otherwise readers are either being misled about the purpose, and significance, of the study or, (worse), the study design does not match the research questions being posed.


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: SHORT AND LONG-TERM EFFECTS OF A SYNBIOTIC ON CLINICAL SIGNS, THE FECAL MICROBIOME, AND METABOLOMIC PROFILES IN HEALTHY RESEARCH CATS RECEIVING CLINDAMYCIN: A RANDOMIZED, CONTROLLED TRIAL
Review round: 1
Reviewer: 1

Output:
Basic reporting: This paper is clearly written in professional English throughout. Literature references and field background certainly are sufficient. Article structure, figures, tables and raw data are clear. There is, however, as the authors admit themselves in the discussion, a problem with the relevance of the results to the hypothesis (a synbiotic will affect food intake, vomiting, fecal scores, fecal matabolome and fecal microbiome during a treatment with clindamycin): insufficient power due to low number of animals. The discussion is very lengthy, with many repetitions.
Experimental design: this is original primary research within aims and scope of the journal. The research question is well defined, relevant and meaningful. The knowledge gap is, however, essentially limited to cats. The local ethincal committee has evaluated the ethical standard. One may question whether this investigation was carried out rigorously. indeed, Indeed, the time lapse between defecation and collection and safe storage of fecal samples is not indicated and may account for the lack of clear and unambiguous conclusions with respect to the effect of the synbiotic. Moreover, some indication is given as to the prebiotic strains included, but there is no information regarding the prebiotic included in the synbiotic. It looks as if the synbiotic contained glutamate to improve palatability, since glutamate was the most important change in the metabolome associated with treatment. there are some problems with the experimental set up and the methods used. there is no control group without antibiotic treatment. The number of animals is insufficient, resulting in underpowering.
Validity of the findings: A follow-up study with a better experimental set up by the same group has already been published (Stokes et al., 2017). Data are insufficiently robust. Sensitivity of the probiotic strains to the antibiotic was not tested. The discussion about Clostridium difficile is irrelevant in cats.
Additional comments: The effects on the microbiome could be partly explained by difference in time lapse between voiding of the faeces and safe storage.