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: INTERACTION OF GUIDANCE TYPES AND THE NEED FOR COGNITIVE CLOSURE IN WIKI-BASED LEARNING
Review round: 1
Reviewer: 1

Output:
Basic reporting: The introduction, method and results sections are very well written and are clear, while the discussion and conclusion are less clear and contain more errors, although still clear. I'd suggest that a native English speaker proof reads these two sections.

The abstract doesn't misrepresent the results of the paper, but could be clearer about the actual findings, which are (in my opinion) somewhat less interesting than might be assumed from the abstract, rather than simply hinting about 'effects'. e.g. a short list of how the guidance types affect user behaviour and how NCC interacts with 'learning outcomes', namely the test score (e.g. the sentence starting line 455).

Similarly, the non interactions of the study variables are ignored in the abstract. e.g. line 419, "In summary, the analyses suggest relatively small to virtual no effects on the interaction between guidance and the NCC on all the process variables" or the line 469.

Figure 2 is too small to read.

The abbreviation DDR is introduced on line 118, but isn't defined anywhere I could find.

On this topic, the language used is sometimes mixed, e.g. implicit vs. explicit guidance, highlights vs. script, icons vs. DDR, etc. Although it's pedantic, I think you should pick one way of referring to the two wikis and use it consistently throughout the introduction, results and conclusion.
Experimental design: I'm tempted to put this paper more in the area of Social Sciences, or the Humanities rather than clearly in the areas of Biological Sciences, Medical Sciences, or Health Sciences.

The design and motivation of the experiment is good and the study rigorous. The methods are clear.
Validity of the findings: The statistical analysis looks robust to me (not technical expert). I'd recommend that at least one of the reviewers be professional statistician.

One control which could be interesting is a wiki without any guidance, implicit or explicit, but I think the authors mention their previous work in this area. This could probably be made clearer.
Additional comments: The work is good and the introduction is very interesting and flows well.

I think you should be clearer when you're citing your own work. e.g. 'we have previously shown...' rather than, 'previous experimental studies have shown...'.

NCC is mentioned on line 50 of the introduction, but isn't described until later in the paper (line 105). I'd be happier if it was described the first time it is mentioned.

Why is this RQ5? what happened to RQ1-4?

I'd be interested in an evaluation of the quality of the final articles.

Sorry for the dumb question, but, why is the mean selection difference of 0.48 (line 319) not simply 4.60 - 4.21? e.g. 0.39?

Does Figure 5 show statistically significant differences? This could be clearer.


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: INTERACTION OF GUIDANCE TYPES AND THE NEED FOR COGNITIVE CLOSURE IN WIKI-BASED LEARNING
Review round: 1
Reviewer: 2

Output:
Basic reporting: 1/ The title is not relevant.
- The "scaffolding" term is undefined in the article.
- The study design is not mentionned (laboratory experimental study).

2/ Background and research justification are unclear
Theorical concepts in introduction are exposed confusingly, and the relevancy of the research questions is not understandable. It is only at the beginning of the discussion (lines 452-460) that the real point of interrest of the study seams to appear...
We would be greateful to the authors:
- to expose clearly in introduction the fact that this study is a continuum with prior works. Please avoid citing oneself as any else author (l. 48-49)
- to recall main findings of their anterior studies and to explain more directly the relevance of this further investigation before exposing research questions and hypothesis (l. 119-130 and 141-147 are unexpected at this stage). Does the research question number "RQ5" indicates that this paper is only a part of a larger research framework ? If yes, please state. If no, please explain.
- to deepen the state of the art regarding to the study concern: are there other studies focused on NCC and collaborative learning guidance ?
- to avoid using concepts without defining them ("need for cognitive closure" appears at line 50 while it is only defined at line 103)
- to shorten long sentences, especially those referring to complex theorical knowledge (l. 43-45)
- to cite litterature accordingly to affirmations
    -- l. 22 - Choy and Ng 2007: we expect a paper giving an idea of the prevalence of the use of collaborative learning tools in higher education, not a single experimentation report
    -- l. 24 - Notari et al. 2016: we expect a descriptive paper about uses of wikis within the educational field, not a referrence to a method for constructing educationnal wikis. At least, indicate the pages in this book giving such a description.
    -- l. 31-33: no citation. Referring to the athors' prior works ??
  (...)
- to lighten the theorical background exposure when having no impact on the study's relevancy (l. 21 - 115)
- to give a definition for every acronyms (l. 118)
Experimental design: 3/ There is a damaging lack of correspondance between the research questions (RQ), the methods and the results
The reader can not link findings to the RQ nor to the methods:
- the RQ terms 'individual selection', 'reply behaviour' and 'individual contribution' do not match the results terms 'topic selection', 'topic contribution time' and 'topic frequency' without explanation.
- the methods terms exposed in "Measuring process variables" (l. 273-283) do not match the result terms  'topic selection', 'topic contribution time' and 'topic frequency':
  -- it seems that the results' "topic selection" correspond to the methods' "click on talk page titles" ? - please explain
  -- to what correspond the results' "contribution times" in the methods ? article reading time ? talk threads reading time ? article edition time ? talk threads response edition time ?
  -- to what correspond the results "reply frequency" ? article's chapters ? talk threads ?
- RQ, methods and results do not follow the same plan, which makes the cross-reading extremely difficult.
We would be greateful to the authors to clarify the terms used and to harmonize RQ/methods/results.

4/ The Methods needs clarifications
- how were recruited participants ? according to which criteria ?
- there is no description of the origin of participants recruited out of the university (N=13)
- there is no description of gender, age nor origin distribution within groups
- while using t-test based statistical tools, it would be welcome to test the normality of the distribution of NCC values (l. 248-261)
- statistical calculations upon the knowledge test are made without giving a description of it (l.177-179): we need at least the scale of the test to appreciate the 1 point minimal effect size of interrest.
- the participant's topic interrests/prior knowledge are presented without having exposed which is the topic concerned (l. 192)
- the "base wikipedia-like" article is mentionned (l.211) before it's description (l.229 and further)
- figure 1 is extremely simplified according to the real participant's process. It does not allow a better understanding.
- the "3 phases of 7 minutes" (l.217) need deeper description as they seem to impact the results understanding (what really mean "topic reply frequency" ?)
- !! this is an important point as it sustain all the study: the description of the wiki environment and the two types of guidance need to be improved (l.234-246 and figure 2)
  -- a screenshot of the article would be welcome
  -- avoid using undefined acronyms ("DDR") or familiar words ("bogus")
  -- comparative screenshots of both groups with more explanations are needed:
    --- in the implicit group: authors should legend flags colors meaning
    --- how look like the same screen for the explicit group ? how and when appear explicit guidance messages on screen ? how does the participant's choice (1/2/3/(4?)) affects the page edition ?
    --- the diagram on the right of the figure 2 is disconnected from the text description
- the dataset contains 'TimeResolved', 'TimeUnresolved', 'ReplyResolved', 'ReplyUnresolved','ArticleLength' and 'ArticleDifference' colums that do not match with methods description nor results terms. Authors should precise:
  - what include 'TimeResolved' and 'TimeUnresolved' items: talk reading ? article reading? talk response ? article edition ?
  - how were considered 'replies' contributions: only in talks? including the correspondant section in of the article ?
  - why authors did not mention the articles' length in their paper while having measured it ? Please justify every step of your work, even abandonned branchs.
Validity of the findings: 5/ The results exposure is unclear
- results should not include methods (l. 301-315, 385-394)
- as already pointed, results should follow same items than RQ and methods
- Figures 3 and 4 do not improve the understanding. Authors should report every measure (topic selection / contributon times/reply frequency/knowledge test) or none.
- The knowledge test interaction between guidance and NCC analysis do not report the effect of the covariate "prior knowledge" which is supposed to have been tested.
- Figure 5 shows the linear regression result with points dispersed on a 0-25 scale ordinate as the test score ranks 0-18: ?

6/ Lacks in the presentation of the findings (discussion/conclusion)
In Discussion, we would appreciate that authors discuss strength and weakness of their work, in particular:
  - the fact that most participants are Applied Cognitive and Media Sciences students is a limitation in results extrapolation (which is developed in conclusion ... )
  - the fact that the study design and methods were adapted to existing tools (implicit and explicit guidance processes) rather than having creating tools on purpose.
  - these findings seems to be of some interrest to improve individually-fitted collaborative learning processes. However, the "real life" extrapolation of these findings should be discussed.
As already expressed, the validity of the findings is impaired by the lacks in methods. In particular, we need to better understand the correspondance between the results and the participants' tasks.
The Conclusion is actually a Discussion. We expect there a brief synthesis of main findings in order to replace them in the general context, eventually followed by an opening.
Additional comments: 7/ The scope of this paper is at the fronteer of the cognitif sciences. It is more relevant to educational sciences & informatics.

Thanks to the authors for this work, and to the editorial team of PeerJ to trust my expertise.


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: INTERACTION OF GUIDANCE TYPES AND THE NEED FOR COGNITIVE CLOSURE IN WIKI-BASED LEARNING
Review round: 1
Reviewer: 3

Output:
Basic reporting: This was a well structured and clearly articulated article. The literature was well described, although two relatively minor points are: Lines 111-113: Citation needed
Lines 113-115: You mention that there are “only a few studies” that address the concept but don’t provide them. Please clarify and/or provide a further sentence/s here to identify sources that do address it. The diagrams and figures were professionally produced. Hypotheses were clear with relevant results. (Note that there were quite a few typos in the article e.g. spelling of "conclusions" in the final section).
Experimental design: The research fits within the aims and scope of the journal and the rationale for the research is clearly articulated. The research design was relevant to the research questions which were meaningful to current questions relating to the design of wiki tools for collaborative educational purposes.
Validity of the findings: Conclusion is clear and supports the results reached.
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: INTERACTION OF GUIDANCE TYPES AND THE NEED FOR COGNITIVE CLOSURE IN WIKI-BASED LEARNING
Review round: 2
Reviewer: 1

Output:
Basic reporting: I would first congratulate the authors. The article has been significatively improved since the first version. Review comments have been seriously considered and revised accordingly. The global text thread is now well understandable, introduction, methods, results and discussion are coherent, and the justification of the research questions is finally clear.

Some minor comments/questions :
Experimental design: Methods :
- i would have liked to have a brief description of the 13 participants which were not students, and particularly : how are they distributed in the two groups ? (e.g. : would it represent a confusion variable?)

- "Regarding the normality assumption checks of t-Tests. We omitted these results since the equivalence analysis we use builds upon Welch’s and not Student’s t-Test.[...]"

My note aimed at helping you improving the validity of your study, especially since your main finding lays on a variance analysis. I had a look at your NCC's values: they actually seem normally distributed. But that hypothesis should be tested. I agree that the Welsch's correction of the Student's t-test improve the robustness regarding to variance gaps. However, it is not the case regarding to non parametric distributions. Such a weakness would dicrease in large samples, but it is not the case of this study. More critical for your findings: analysis of variances such as (M)ANCOVAs would make no sense in case of non parametric distribution.
Validity of the findings: Results :
- some RQ hypothesis are mentioned to be validated (l 362, 368). However, as results are not layed in the same order as hypothesis are given, and as hypothesis and results are multiple and slightly complex, the reader must go up and down several times through the text to well understand correspondances and meanings. Authors should refer more clearly to their RQ (e.g. «  Subsumed, the results regarding the process variables provide evidence for the hypothesis H1a about the equivalence of implicit and explicit guidance wikis. »). Doing this way systematically for every hypothesis would be greatfull.
-  hypothesis H1b and Topic contribution times : how do you interprete the results ? They show significative differences between groups, but in opposite ways depending on the discussion threads quality (resolve/unresolved). However, « resolved/unresolved » was not a point of the RQ1 ?

Discussion :
- the discussion about the interaction of NCC & guindance mainly concern the hypothesis H2c. What about H2a and H2b, which seem not verified ?
Additional comments: After all, the conclusion is in accordance with the findings, and, moreover, the abstract resumes perfectly the whole study.

This is a quality paper which will be probably usefull in a broader scope than the single wiki-based learning.

Thanks


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: EFFECTS OF MACROALGAE LOSS IN AN ANTARCTIC MARINE FOOD WEB: APPLYING EXTINCTION THRESHOLDS TO FOOD WEB STUDIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: The major claim of this paper is to investigate how the Potter Cove food web respond to loss of macroalgae species, as a consequence from ongoing climate change, a question of high importance and relevance. The authors use a well-defined method, so called topological approach, and conclude that the community is highly robust to extinctions of the major source input, i.e. macroalgae. The manuscript is well structured but less well written. I have a number of comments (major and minor) that I believe should be addressed before the manuscript is considered for publication.

Comments for improvements:
1) The English language needs to be improved throughout the entire manuscript. Examples of such improvements are presented below(strikethrough shows words suggested to be removed, and italic underlined words are suggested to be added):
a.	Row 20. Over the last years, Potter Cove annual air temperatures averages increased with 0.66°C.
b.	Row 31-33. This result is dramatically different from that found in other food webs where by simply reducing 10% of prey intake caused a disproportionate increase growth of secondary extinctions was observed.
c.	Row 43. Antarctica is one of the regions most seriously…
d.	Row 86-88. Borvall et al. (2000) studied the effect of omnivory and redundancy in model food webs and found that both lessen the risk of cascading extinctions following further primary loss of species.
e.	Row 96-98. For this these reason, we proposed to study the robustness of Potter Cove food web by simulating primary loss extinctions of macroalgae species using a topological approach.
f.	Row 147. In this manner, secondary extinctions occur are produced when one consumer species lose losses all of its preys prey species.
g.	Row 322. “…massive pulses of certain species and the strength of each interaction are required to satisfactory predict the impacts of climate change on the currently threatened Antarctic marine ecosystems of Potter Cove”.

2)	I cannot find the corresponding figure texts.

3)	Please link the result sections to the described analysis in the method part using the same subheadings.

4)	Check all the references, some of them lack information of Journal volume, issue, and page number. Also go through points and comma.

5)	Perhaps the terminology of adjacency matrix could be renamed with the term predation matrix, which is more commonly used in the field of community ecology.

6)	Consider changing “detritus” in row 25 to detritivores (as I believe detritus do not itself need energy).

7)	Explain the meaning of thresholds of extinction in the summary part.

8)	In the summary and on row 302 the authors write that the similarities in the results between the two extinction sequences “ascending biomass” and “descending degree” could be explained by the involvement of key species which have an emerging effect on the food web. Could the authors discuss more about this? Any ideas of common characteristic of these “key species” that could trigger the same food web response when lost?

9)	Please add more information to the figure axis. For example the x-axis in fig 3-5 could be named Primary extinction (%).

10)	Please add more information of the food web under row 116 Food web dataset. How many species does the food web of Potter Cove consist of? Range of trophic levels in the food web?

11)	Consider change the meaning on row 221 “It was observed that when we increased the number of secondary extinctions,…” to “It was observed that when the number of secondary extinctions increased,…”

12)	Incomplete meaning on row 244 “The analysis of secondary extinctions showed a general increase trend with threshold (0% threshold, secondary extinctions=6.5 %; 25% threshold, secondary extinctions=9.8%; 50% threshold, secondary extinctions=29.5%; 75% threshold, secondary extinctions=50.6%), and a logical increase with primary extinctions (Fig. 5).”
a.	Add to the first part of this sentence “The analysis of secondary extinctions showed a general increase trend… -> in what?.
b.	Even though it is a logical response of increased number of secondary extinctions following primary losses, explain this logical part.
Experimental design: Comments for improvements:
1)	The authors needs to carefully describe their definition of thresholds used in the study. In the method part (row 158), they write that a “threshold represents the amount of energy and matter intake that triggers the extinction of one species.
a.	Here, please describe how energy intake trigger secondary extinctions in a topological model where secondary extinctions are caused by loss of prey-species (i.e. loss of energy intake).
b.	Furthermore, the authors write on row 159-161 that “A threshold of 0% corresponds to the classical topological approach where species extinctions are mediated by the loss of the whole prey set of a consumer.” This contradicts the method description on row 156-157 saying that the authors follow the concept by Bellingeri & Bodini (2013) who considered that a species went secondarily extinct once is lost at least 25%, 50% or 75% of its original number of prey-interactions. The authors also states on row 197-198 that the extinction threshold represents the percentage of prey that a predator has to lose to go extinct. However, this is not the way the results are presented. I believe the authors define an extinction threshold as the number of interaction links left after a primary extinction (e.g. when a consumer has 0% of its interaction links left (i.e. no prey-interactions) (or 25%, 50% or 75%), than the consumer goes extinct). Please be consistent with your definition of extinction threshold and make sure that the text in the manuscript and figures describes the results following this definition. As now, this creates confusion.

3)	On row 61-63, the authors briefly present a study (Marina et al 2018) that found the Potter Cove food web to be fragile to species loss, using topological analysis. Please explain the differences between this study and the current manuscript. For me, they show highly similarities.
Validity of the findings: Comments for improvements:
2)	Add to the discussion of the differences between a topological approach and a dynamical approach simulating species loss. The authors mention, staring on row 307, that dynamics can influence the stability of food webs. Nevertheless, they do not discuss important mechanisms such as the lack of top-down cascades in topological methods and its influence on stability.
3)	The conclusion of the study, presented on row 331, is to strong, saying that the results undoubtedly demonstrate the structural robustness of the Potter Cove to loss of macroalgae species. In face of the discussion part saying that the food web includes all nodes and interactions (without considering effects of seasonality and pulsatile nodes and interactions) in combination with the use of a topological approach known to provide more robust results compared to dynamical approaches, the conclusion should be presented in a more discrete manner.
Additional comments: I have now reviewed the manuscript by Cordone et al, entitled: Effects of macroalgae loss in an Antarctic marine food web: applying extinction threshold to food web studies. The authors present an analysis of food web robustness using a well-known method (topological extinction approach) which has been used to evaluate the impact on species loss in many food webs, making it difficult for this specific paper to fill a general knowledge gap. However, the robustness analysis has not, of course, been conducted for this specific food web of Potter Cove. The study is in its basic well done, but less well presented. As now, the result are not presented the way the method describes it causing confusion. I would not recommend this paper for publications as it stands today. However, I do believe the authors could make substantial improvements making the manuscript attractive to publication later on.


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: EFFECTS OF MACROALGAE LOSS IN AN ANTARCTIC MARINE FOOD WEB: APPLYING EXTINCTION THRESHOLDS TO FOOD WEB STUDIES
Review round: 1
Reviewer: 2

Output:
Basic reporting: I believe that the article is well structured and the subject of study is well explained.
The research question is showed to be relevant, well presented, and resolved.
The authors also do a good use of references to back their assessments and work.

As regarding the use of English, I would recommend a little revision of the English used in the document, since apart from some faults (ex. there is a missing "a" in the abstract as in "a hot biodiversity spot") the style sometimes is a little bit confusing.

The general structure of the article is well established and makes sense for the reader.
However I feel that some improvement should be done in the methods section to improve the clarity of how the experiment is carried upon. Also, I have some minor issues with the graphics that I think should be clarified to improve the readability of the manuscript.

In all, I believe it is a good research work. However, I feel I need to clarify how some of the work has been carried upon before accepting the manuscript.
Experimental design: My mayor issue is with the methods sections:
The most important is that even if the authors provide a good background of how are the topological extinctions performed in the cited literature, they do not provide a clear explanation of how they implement it. The points I think should be more clearly explained are:

     -1) How do you obtain the “post-extinction” community ?:
 In the manuscript you say : "Simulations consisted in remove(ing) target species from adjacency matrix deleting row and columns. Following every extinction simulation, a new adjacency matrix was computed, and several [quantities ...] were calculated", but How do you compute the new adjacency matrix? When do you consider that a species is extinct, when it has no more partners? Or when they are disconnected from the basal resources?
It is true that when doing extinctions  in mutualistic networks it is enough to consider that a species undergoes extinctions once it has no more (or no more than a threshold) partners. However in trophic communities a species should go extinct not only if it has less than x partners, but also if it is no longer connected to the basal species in any ways (see Googling Food Webs: Can an Eigenvector Measure Species' Importance for Coextinctions? https://doi.org/10.1371/journal.pcbi.1000494).
I don't think your method of obtaining the post-extinction community it is clear enough in the manuscript as it is, and in order to make it more amenable to replication it should be further explained.

    -2) How you perform the extinctions:
It is also confusing the way in which you carry on the extinctions. You say first “We defined different sequences of extinctions considering  [topological properties ...]” ,  “After the loss of all macroalgae species, we removed the two sources of detritus” . So I understand from here that you erase ALL basal species in different order. If that is the case, then, how can it be possible that even if all basal species are lost there are still more than 100 links remaining in the community at the end of the extinctions? (see figure 3). Is it because there are still some basal species left? If that is, why do you attack the detritus but not these others? If, on the other hand you are attacking all basal producers, why do you still have a community remaining?

   -3) Foodweb picture:
Finally I think that the manuscript could benefit from including the foodweb image in the main article and not it the supplementary. Since it is that community the one under attack it makes sense to me to show it in the article so readers can have a general idea of how it is. Maybe you could make a combined figure 2 with the common-enemy graph and show both at the same time?...
Validity of the findings: My first concern is with how the post-extinction community is obtained. I really think that in a foodweb one should consider that a species is extinct not only when it has no more prey, but also if it is no longer connected by any path to the basal producers. I'm not sure if the authors have taken this into account as I commented before ... In the case where they didn't I also believe that given the high connectance of the network the results should be similar even if this is taken into account. I suggest the authors should try to consider this in order to obtain a more realistic outcome of the topological extinctions.

My second concern regarding the results is with the last picture of figure 3, 4 and 5 (75% threshold image). In those images the x-range goes from 0 up to 60, when previously the authors have stated that they only have 40 species of macroalgae in the foodweb.  How is it possible then to erase up to 60? If, on the other hand, what is reflected in the x-range is the percentage of attacked species it should be clarified in the figure someway. In that case, why do you erase only up to 40 or 60 %?

Finally I think that both the increasing and decreasing degree should be performed more than once due to the high degeneracy in the degree sequence (that is, many species have the same degree but they may have a different impact when erased from the community). I don't think it is going to have a real impact in the results at all but for the sake of completion I think it would be better to perform a similar study as they do with the random sequence, where they provide the average result and the deviations.
Additional comments: I've enjoyed reading the work, and I think it's really interesting.
However I believe these points should be clarified before publishing, to ensure maximum readability of the manuscript.


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

Input:
Title: EFFECTS OF MACROALGAE LOSS IN AN ANTARCTIC MARINE FOOD WEB: APPLYING EXTINCTION THRESHOLDS TO FOOD WEB STUDIES
Review round: 2
Reviewer: 1

Output:
Basic reporting: I've now read the new version of the manuscript, and I think that the authors have made a great improvement in the readibility of the manuscript and that it can be now accepted to be publisehd.

They have clarified the doubts I had with the methods and I believe now all readers can easily understand the procedure employed to perform the analysis.
The authors also made all the changes I suggested to the figures and I think they are more clear now, and all legends and axes are unambiguously described.
Also the authors present their results in perspective by mentioning how topological extinctions could overestimate the robustness of the foodweb, and taking into consideration the possible effect of temporal dynamics on the analysis.

All In all, I believe the authors have made a great effort in improving the quality of the manuscript, both by clarification of their methods and figures as well as the general writing, and I believe the article is ready to be published.

I'd like to note some minor faults I found during the lecture in case the authors would like to consider them:
line 33: Potter Cove food web is relative[ly] robust to macroalgae ...
line 47: is the most affected region of Antarctica due to climate change ->  is the region most affected by climate Change
line 55: effects on [the] organisms of the cove
line 62: at [the] benthic
line 123: on [the] food web presented by Marina
Experimental design: The methods is clearly presented now in the supplementary information.
Validity of the findings: I believe there is a mistake in line 256:
The authors state : "When we compared the responses at different v, we found that an increase in v led to a decrease in the number of lost interactions (Lmin values of 211, 197, 129, and 30 for v of 0, 25, 50, and 75 %, respectively)."

I guess the authors mean that an increase in v leads to an INCREASE in the number of LOST interactions, as Lmin decreases when v is increased and vice-versa.
Additional comments: I'd like to thanks the authors for making the raw data and code available for all readers. I think sharing the methods and making the results easily reproducible is really important in science.


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: DEEP DIVERGENCE OF RED-CROWNED ANT TANAGER (HABIA RUBICA: CARDINALIDAE), A MULTILOCUS PHYLOGENETIC ANALYSIS WITH EMPHASIS IN MESOAMERICA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors present their research on the phylogeographic history of the Neotropical bird species complex, Habia rubica. The sampling covers the entire geographical distribution of the species. However, a very similar study of the same species, which is cited by the authors (Lavinia et al. 2015), also used samples covering the entire distribution. In that study, the species complex was most strongly sampled in the Atlantic Forest and Amazonia, while the present study sample favors Central America. Lavinia also utilized a much more complete data set (DNA sequencing, morphological and vocal analysis) than found in the present study which relies exclusively on DNA sequencing. Therefore, this paper does not contribute a great deal of new information to what is already known about the taxonomy and biogeographical history of Habia rubica across its entire distribution. The most important contribution of this paper is the extensive sampling in Central America, reveling new clades not described by Lavinia. However the discussion is weak, especially since the authors do not develop a comparison with the findings of Lavinia. I feel that this manuscript has the potential to be an important and interesting contribution if the authors can refocus and reexamine their data to a regional scale, restricted to biogeographic issues of the species in Central America that were not sufficiently described by Lavinia. The title should be modified giving emphasis to phylogeography on a regional scale (Central America). I also suggest not emphasizing taxonomy since the only method used was DNA sequencing, unlike the more extensive morphological and vocal analysis found in Lavinia.
Experimental design: Line 153 - How was convergence in the Bayesian run determined? Many authors simply use TRACER, but this may not be sufficient. I suggest using AWTY in addition to TRACER to determine if the tree topology had reached convergence. While overall tree likelihoods and individual model parameters reach convergence in less than 3 million generations, the tree topology requires up to 8 million generations to reach convergence. In general, I suggest using a minimum of 20 or even 50 million generations for Bayesian analyses in MrBayes and then using a very generous burn-in. In contrast, you use a 100 million generation sampling strategy for BEAST which seems good!

Line 197 – Why Yule process? Yule process assumes that there are no extinctions, which could occur here.
Validity of the findings: no comment
Additional comments: The authors present their research on the phylogeographic history of the Neotropical bird species complex, Habia rubica. The sampling covers the entire geographical distribution of the species. However, a very similar study of the same species, which is cited by the authors (Lavinia et al. 2015), also used samples covering the entire distribution. In that study, the species complex was most strongly sampled in the Atlantic Forest and Amazonia, while the present study sample favors Central America. Lavinia also utilized a much more complete data set (DNA sequencing, morphological and vocal analysis) than found in the present study which relies exclusively on DNA sequencing. Therefore, this paper does not contribute a great deal of new information to what is already known about the taxonomy and biogeographical history of Habia rubica across its entire distribution. The most important contribution of this paper is the extensive sampling in Central America, reveling new clades not described by Lavinia. However the discussion is weak, especially since the authors do not develop a comparison with the findings of Lavinia. I feel that this manuscript has the potential to be an important and interesting contribution if the authors can refocus and reexamine their data to a regional scale, restricted to biogeographic issues of the species in Central America that were not sufficiently described by Lavinia. The title should be modified giving emphasis to phylogeography on a regional scale (Central America). I also suggest not emphasizing taxonomy since the only method used was DNA sequencing, unlike the more extensive morphological and vocal analysis found in Lavinia.

A few more comments:
Abstract
Line 32 – I suggest adding more information about Habia rubica, when is mentioned for the first time.

Methods
Line 153 - How was convergence in the Bayesian run determined? Many authors simply use TRACER, but this may not be sufficient. I suggest using AWTY in addition to TRACER to determine if the tree topology had reached convergence. While overall tree likelihoods and individual model parameters reach convergence in less than 3 million generations, the tree topology requires up to 8 million generations to reach convergence. In general, I suggest using a minimum of 20 or even 50 million generations for Bayesian analyses in MrBayes and then using a very generous burn-in. In contrast, you use a 100 million generation sampling strategy for BEAST which seems good!

Line 197 – Why Yule process? Yule process assumes that there are no extinctions, which could occur here.

Results – no comments
Discussion – Should be refocused to a regional scale with a reduced stress on taxonomy.


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: DEEP DIVERGENCE OF RED-CROWNED ANT TANAGER (HABIA RUBICA: CARDINALIDAE), A MULTILOCUS PHYLOGENETIC ANALYSIS WITH EMPHASIS IN MESOAMERICA
Review round: 1
Reviewer: 2

Output:
Basic reporting: There are some small editorial issues to address. A good copy editor would help. Comma use is sometimes hard to follow. Fig. 3 tip labels have low resolution.
Experimental design: Sampling is generally good. Only the Venezuela population is a problem, but that is noted in the results.
Validity of the findings: The authors study the genetic structure of populations of a Neotropical bird, Habia rubica. They use one mtDNA and four nuclear loci to produce a tree, to do species delimitation using BPP, and to date divergence times. The results are concordant with major geological features in the taxon’s range, and they find seven lineages that they conclude are species.

The authors used 125 H. rubica from most of the range and used appropriate outgroups. 37 of these were also sequenced at 4 nuclear loci. It is a good study and with a few improvements will better.

One concern is that the authors are using a very simplistic concept of species – what we might term a BPP species. Is this concept widely accepted in ornithology? Barcoding “species” were not considered acceptable to ornithology when I last paid attention. This is not very different from that. In fact, a recent paper that the authors do not cite has done simulation studies to show that BPP will often misdiagnose populations as species (Sukumaran and Knowles, 2017, PNAS 114: 1607).

This leads to the next issue, which is to disregard all other data except the genetic data. It is touched on that the phenotypes disagree with the reconstructed tree, but little is made of this, either in discussing why we might expect 17 phenotypes found to not match 7 genetic lineages or to provide more evidence for the recommended taxonomy. In this the authors go directly against the recommendation of the PNAS paper cited above.

It would be good to know how much genetic variation is present within the in-group for the markers used. We have seen a number of cases in which mtDNA has not provided an accurate phylogeny, and these cases have only come to light with the addition of substantial amounts of nuclear data. It is good that the authors have four nuclear loci (2,716 bp) against the 1,041 bp of mtDNA, but we do not get a summary of how much information is in those loci for the in-group questions, so the mtDNA are still likely driving a lot of the relationship that is reconstructed. In a quick scan of the data on figshare it looks like the nuclear loci are not very information rich for the in-group compared with mtDNA, so quantifying that would help the reader.

A key assumption in dating nodes on the phylogeny is that the species historic distribution was affected by the two geological events used to base divergence estimates. This is a big assumption. It is also not necessary to rely on it alone, because the mtDNA gene ND2 has been extensively studied and has its own mutation rate. This provides an independent check and would be easy to implement.

So I think there are three major issues: 1) the species concept used and the published evidence that BPP oversplits by recognizing populations as species. 2) the relative amounts of information in the mtDNA and nuclear DNA for the ingroup (easily summarised). 3) using ND2 for a second set of divergence estimates so you don’t have to rely alone on the assumption that the species was present and affected by the two geographic events used currently to date the nodes.

In addition, there are some minor issues:

Why figshare? This is an unusual place to archive sequence data. Having the alignments used is useful, but it would also be useful to archive sequences on GenBank with the museum voucher numbers.

I notice that the Lavinia et al. 2015 paper recommended recognition of three species, whereas here the recommendation is seven. That should be discussed more because they included phenotypic analyses. (It also looks like the Venezuelan population would almost certainly emerge with more individuals as another BPP species.)

The Lavinia paper also does a better job with geography in the text and their figure 1. The authors might look at that because I think their treatment could be clearer.
Additional comments: See 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: DEEP DIVERGENCE OF RED-CROWNED ANT TANAGER (HABIA RUBICA: CARDINALIDAE), A MULTILOCUS PHYLOGENETIC ANALYSIS WITH EMPHASIS IN MESOAMERICA
Review round: 1
Reviewer: 3

Output:
Basic reporting: A Multilocus phylogenetic analysis provides evidence of deep divergence between populations of Red-crowned Ant Tanager (Habia rubica: Cardinalidae).
The authors claim to investigate the genetic structure of Habia rubica populations using a multilocus dataset, five molecular markers were employed and a total of 4.798 nucleotides were used in the analyses. They hypothesized that the species form three main clades: 1-Mexican Pacific coast populations, 2- east of Mexico to Panama, 3-South American populations. The lineages identified within the clades were delimited by geographical barriers in Central and South America and a strong influence of the morphoclimatic domains of South America separating the populations too. The lineages were not congruent with the previously described subspecies. The authors suggested a taxonomic reformulation for Habia rubica.
Experimental design: The methodology was adequated. I suggest few modifications:
1# The information from lines 106 to 110 can be placed in the acknowledgments.
2# I understand that the authors calculated the demographic tests for the different lineages, however, populations from different localities were placed together, which makes the information of table 1 less representative, once the authors mixed different populations together. Therefore, I suggest moving this table 1 to supplemental information.
3# Could you please include the pairwise mismatch p-distances between the lineages? I want to see how distant are the lineages, and if the distance is around 4 to 5%, what is normally observed at species level.
Validity of the findings: Despite the interesting results and the strong support of the phylogeny, the manuscript seeks to investigate the evolutionary history of the Ant Tanager, that have been already published in a recent study “Lavinia et al. 2015 Continental-scale analysis reveals deep diversification within the polytypic Red-crowned Ant Tanager (Habia rubica, Cardinalidae). Molecular Phylogenetics and Evolution, 89:182-193.” Both studies have similar objectives, however, the data analyses were based on different molecular markers and the authors include more samples and more localities, which, I think, reinforce the importance of the results. Overall, both manuscripts displayed of a similar outcome. Then, I think the article is adequate for publication by the PeerJ journal, but it would also be more interesting for publication in an ornithological-specific journal.
Additionally, I was really intrigued by the composition of Clade G: Southwest Brazil, Paraguay, Argentina and Venezuela (Line 231, fig. 1). How the authors hypothesize this close relationship between those populations? Is there a possibility to mistakenly grouping these lineages together? That might also reinforce the status of this lineage as a taxonomic unit with a distinct biogeographic history.
Additional comments: Lines 290-296, The authors could add the time of emergence of the geographical barriers in order to trace a parallel together with the molecular time estimation proposed to the studied species.
Extra space on line 267.


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: DEEP DIVERGENCE OF RED-CROWNED ANT TANAGER (HABIA RUBICA: CARDINALIDAE), A MULTILOCUS PHYLOGENETIC ANALYSIS WITH EMPHASIS IN MESOAMERICA
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The authors have now dealt with all my comments on the first round of revision and I feel the manuscript is greatly improved. The revised manuscript clarifies many of the issues in the earlier version, so it is much stronger now. I have no major concerns with this paper


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: DEEP DIVERGENCE OF RED-CROWNED ANT TANAGER (HABIA RUBICA: CARDINALIDAE), A MULTILOCUS PHYLOGENETIC ANALYSIS WITH EMPHASIS IN MESOAMERICA
Review round: 2
Reviewer: 2

Output:
Basic reporting: Fail. Some previously addressed problems remain and a new one appears (wrong definition of Pleistocene in its beginning date). Details in General Comments below.
Experimental design: Pass.
Validity of the findings: Conclusions remain problematic in some respects. Details in General Comments below.
Additional comments: PeerJ “Deep divergence of Red-crowned Ant Tanager...”

This is the second time that I have read this manuscript. The authors have made some improvements. There are still some places where it might be improved, including where efforts are given in the response but not added to the paper.

Geographic isolation is usually not a criterion for species delimitation. It is easy for isolated populations to become genetically distinct, but that is not usually enough to recognize them as species. Also, you cite de Quieroz (2007) in the response, but not in the paper. It is important to tell the reader what your framework is and how your results do or do not match it.

I am surprised that the authors chose not to cite the Sukumaran & Knowles 2017 PNAS paper. It shows very clearly one of the major weaknesses of these kinds of BPP analyses and that oversplitting is an expected result. The authors themselves respond that they “are well aware the BPP tends to over estimate the number of true species.” But we do not have a presentation of how the authors determined that their results are not such a case of oversplitting. It is interesting to see a recommendation (paragraph at line 357) that we can’t use “only morphological criteria” for species delimitation, but that the authors view of the future seems to exclude it, which seems opposite to the current direction of taxonomy in most groups (integrative).

My earlier suggestion on independently estimating dates using ND2 as a separate check on the dates obtained using geological events alone (which require key assumptions the birds may not have followed) was not directly included. The response says that the estimates were made, but the Methods do not include information on the mutation rate chosen and the Results do not include mtDNA divergence estimates in the Divergence times section. The response goes on to say that the topology is similar and the clades are well defined, but this is not the point. Dating is. What are the ND2 dates, and how do they compare to the ones that are presented? These mtDNA estimates should be present if only to be able to make direct comparisons to the many previous studies only using mtDNA to study these splitting events across these major geographic barriers. The problem becomes most apparent when we examine Fig. 3, in which the two biogeographic events used for the molecular calibration are highlighted. Because they are the drivers of the relationship of the tree to the timeline, the results are more than a little circular. Use ND2 and give us more confidence. Okay: I see now inclusion of the p-distances in response to Reviewer 3 (Table 1). But please use these to tell us what key node dates are on Fig. 3.

Examination of Fig. 3 also indicates to me that the authors are not using the correct definition of the Pleistocene, which began about 2.6 Mya. If Fig. 3 is correct on its dates, then most of the 7 clades (A-G) probably did arise in the Pleistocene, and all of them may have. The Discussion (lines 332-336) should be adjusted to this.

Some additional issues:

The clades A-G are not aligned well with the tree in Fig. 3.

The table included in the response “Table #” should be added to the paper. So should the Phylogroups table. I would put the former in the main text and move the other one to Supplemental Information.


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: DEEP DIVERGENCE OF RED-CROWNED ANT TANAGER (HABIA RUBICA: CARDINALIDAE), A MULTILOCUS PHYLOGENETIC ANALYSIS WITH EMPHASIS IN MESOAMERICA
Review round: 2
Reviewer: 3

Output:
Basic reporting: The authors included the suggestions made by the reviewers in the new version of the manuscript. I believe that this article can be published in the Peer J journal.
Experimental design: The experimental design attended the expectations.
Validity of the findings: The main findings of this study was the improvement of the resolution of the evolutionary history of the populations from Habia rubica distributed along the Mesoamerica area, additionally their dataset brings a larger sample size and wider area covered when compared with the study of Lavinia et al. (2015). Although, the study from Lavinia published in 2015 brings similar results as proposed by the authors in their study.

The well-supported phylogenetic tree and the pairwise p-distance suggest the validity of the results and proposition of taxonomic review for Habia rubica, what can be further validated together with bioacustic and NGS analyses.
Additional comments: No comments.


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

Input:
Title: THE IMPACT OF CHEMERIN OR CHEMOKINE-LIKE RECEPTOR 1 LOSS ON THE MOUSE GUT MICROBIOME
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript: „The impact of chemerin or chemokine-like receptor 1 loss on the mouse gut microbiome“ by Dranse et al. shows a linkage between chemerin and / or CMKLR1 and microbiome composition. They further provide data on the fecal microbiome when animals were housed in different facilities.

This is a well performed study and the aim of the present investigation is clearly described.
English is fine and citted literature is appropriate.

Data are nicely described and presented (with one exception indicated below)
Experimental design: The experimental design is appropriate. Methods are well described. The authors present original research which is within the scope of the journal.

The aim of the present investigation is clearly described. Analysis of microbiome composition is supposed to help several issues relevant in health / disease. Further, this may be one reason for different findings in animal studies performed in different facilities.

Ethical approval for animal studies has been obtained. and results look valid.
Validity of the findings: First study analyzing the microbiome of chemerin / CMKLR1 KO mice. Study design is appropriate and number of animals analyzed is o.k.

Data are well discussed and respective literature is cited and discussed.

Regarding statistics it is unclear whether authors corrected for multiple comparisons,
Additional comments: The manuscript: „The impact of chemerin or chemokine-like receptor 1 loss on the mouse gut microbiome“ by Dranse et al. shows a linkage between chemerin and / or CMKLR1 and microbiome composition. They further provide data on the fecal microbiome when animals were housed in different facilities.

This is a well performed study and the aim of the present investigation is clearly described. Ethical approval for animal studies has been obtained. The experimental design is appropriate and results look valid.

One limitation of the study is that body weight of some mice was not recorded. Authors may measure serum glucose or another well described marker of body fat like adiponectin and evaluate any correlations with fecal microbiota.

It is unclear whether authors corrected for multiple comparisons.

Wildtype mice of the two facilities differ in their fecal microbiota. The authors may analyze serum chemerin to find out whether levels are comparable in both strains.

In figure 1 the graph for WT (CS) is not visible, data have to be shown in a different way.

Minor:
“IBD pathogenesis have demonstrated that local 74 chemerin expression, secretion, and activation increase locally in the colon and are positively associated with severity of inflammation (Dranse et al. 2015; Lin et al. 2014; Weigert et al. 2010).”
Locally or local may be deleted.

“Genomic DNA was isolated from fecal sample samples using the PowerFecal DNA”
please delete “sample”

In “future studies” the term LFD is used but is not explained before.

“In conclusion, this is the first study that investigates the link between chemerin signaling and  microbiome composition“
The term “signaling” may be removed here and elsewhere especially regarding that chemerin knock-out mice do not display major changes in the fecal microbiome. Authors can not be sure that changes observed in CMKLR1 KO are related to chemerin.


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

Input:
Title: THE IMPACT OF CHEMERIN OR CHEMOKINE-LIKE RECEPTOR 1 LOSS ON THE MOUSE GUT MICROBIOME
Review round: 1
Reviewer: 2

Output:
Basic reporting: In the present study, the authors assessed the microbiome composition of fecal samples isolated from WT, chemerin, or CMKLR1 KO mice using Illumina-based sequencing. Chemerin KO and CMKLR1 KO mice were housed at two different facilities and WT mice housed at each facility were used as control. There was a dramatic difference in microbiome composition between two facilities. There were only minor differences in bacterial abundance between WT and chemerin KO mice, but significantly more differences in taxa abundance between WT and CMKLR1 KO mice. Specifically, CMKLR1 KO mice exhibited decreased abundance of Akkermansia and Prevotella, which correlated with body weight in CMKLR1 KO, but not WT. This study is incomplete because the authors analyzed the microbiome composition only after cohousing. The manuscript is clearly written.
Experimental design: 1. KO mice were cohoused with WT mice for three weeks before collection of fecal pellets. What was the reason. As this reviewer recently reported (J. Immunol. 2018, 200:2174-2185), the composition of microbiota can be markedly altered by cohousing.

2. Fecal pellets were collected from female mice. What was the reason? For example, male mice were previously used in their colitis study.

3. Line 143-144: Mice were weighed. What was the result? Did the authors still detect a difference in the weight between WT and KO mice after cohousing?

4. Line 384-386: It would be valuable to collect----.” This experiment should be done.

5. Line 508-509: The authors cite their previous study and describe that CMKLR1 KO mice develop signs of clinical illness more slowly in an experimentally-induced colitis model (Dranse et al. 2015). In the study, littermates were used, which may have contributed to the very marginal difference between WT and KO.
Validity of the findings: Data may be clear but the study is incomplete.
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: THE IMPACT OF CHEMERIN OR CHEMOKINE-LIKE RECEPTOR 1 LOSS ON THE MOUSE GUT MICROBIOME
Review round: 1
Reviewer: 3

Output:
Basic reporting: The work entitled "The Impact of Chemerin or Chemokine-Like Receptor Loss on the Mouse Gut Microbiome" by HJ Dransen and collaborator aimed  to detect changes in the microbiota in wild type mice compared to know-out mice impaired for the Chemerin, an adipocyte derived signaling molecule that serves as a ligand activator of Chemokine-like receptor 1(CMKLR1) and the proper CMKLR1. This pathways are responsible for the regulation of metabolism and inflammation processes.

The literature, the structure of the work, the English form, proposed tables and figures are appropriate.

All figures included in the PDF are of very low quality and must be improved.
Experimental design: In general the applied strategy based on 16S rDNA amplicon metataxonomy is acceptable, the authors highlighted difference in gut microbiome by the means of fecal pellet DNA extraction and 16S rDNA amplicon Illumina sequencing, between two groups of KO mice for Chemerin and CMKLR1 from two different laboratory respectively.

Bioinformatics and statistical approaches are properly applied.
Validity of the findings: Main differences have been observed between the mice colonies belonging to the two laboratories participating to the study. Within same facility, WT and KO mice showed very small difference mainly related to few groups of bacteria. Such as Akkermansia and Prevotella, both negatively correlate to body mass as also described in other studies. Although this seems to add few knowledge to the field due to the high dissimilarity in microbiome found between the two laboratories, the author succeeded to reduce the confounding factor of the high microbiome diversity between KO and wild type mice from each laboratory, identifying a correlation with genera (Akkermansia and Prevotella), well known to interact in several gut-related pathologies. In such a way, they demonstrated correlation between these genera and the knocking out of adipocyte signaling pathway.
Additional comments: Minor changes
Just at the beginning of the introduction, Microbiome is described as commensal relationship. This is surely correct but is restrictive. It is widely demonstrated that on top of all possible interactions, the great niche landscape offered by the gastrointestinal tract give space also, for example, to mutualism, strict dependencies, probably parassitism, etc. Please extend a little bit more this state.

Lines 49-51. This number have been recently revised using modern data and bibliographic revision in "Are We Really Vastly Outnumbered? Revisiting the Ratio of Bacterial to Host Cells in Humans" (Cell. Volume 164, Issue 3, 28 January 2016, Pages 337-340), please add this reference.
Lines 65-67, the references cited in these lines are not consistently proposed with the format "(...see (Rourke et al. 2013))." The nested parenthesis could be removed.
68-69, same as previous 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: THE IMPACT OF CHEMERIN OR CHEMOKINE-LIKE RECEPTOR 1 LOSS ON THE MOUSE GUT MICROBIOME
Review round: 2
Reviewer: 1

Output:
Basic reporting: The manuscript: „The impact of chemerin or chemokine-like receptor 1 loss on the mouse gut microbiome“ by Dranse et al. shows a linkage between chemerin and / or CMKLR1 and microbiome composition. They further provide data on the fecal microbiome when animals were housed in different facilities.

This is a well performed study and the aim of the present investigation is clearly described.
English is fine and cited literature is appropriate.

Data are nicely described and presented
Experimental design: The experimental design is appropriate. Methods are well described. The authors present original research which is within the scope of the journal.

The aim of the present investigation is clearly described. Microbiome composition is supposed to be relevant in various diseases. Further, findings presented here may explain variations in animal studies performed in different facilities.

Ethical approval for animal studies has been obtained and results look valid.
Validity of the findings: First study analyzing the microbiome of chemerin / CMKLR1 KO mice. Study design is appropriate and number of animals analyzed is o.k.

Data are well discussed and respective literature is cited and discussed.
Additional comments: Authors have addressed all my previous 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: THE IMPACT OF CHEMERIN OR CHEMOKINE-LIKE RECEPTOR 1 LOSS ON THE MOUSE GUT MICROBIOME
Review round: 2
Reviewer: 2

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


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

Input:
Title: THE IMPACT OF CHEMERIN OR CHEMOKINE-LIKE RECEPTOR 1 LOSS ON THE MOUSE GUT MICROBIOME
Review round: 2
Reviewer: 3

Output:
Basic reporting: The authors fulfilled comments and improved the manuscript accordingly.
Experimental design: The authors fulfilled comments and improved the manuscript accordingly.
Validity of the findings: The authors fulfilled comments and improved the manuscript accordingly.
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: TIBIA FUNCTIONALITY AND DIVISION II FEMALE AND MALE COLLEGIATE ATHLETES FROM MULTIPLE SPORTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper is very well written, but there are a few minor grammatical errors, specifically regarding the use (or lack of use) of commas, that make some lines difficult to read. For example, see lines 61-62 .
Experimental design: 1. The term SSIp appears many times, but is never defined with an equation. A reference to previous development of the parameter is mentioned in the Discussion, but a definition should be in the text and appear earlier.

2. Were the regressions performed all significant? Some of the slopes reported are small (see Fig. 1B) and the correlations may not be statistically significant.

3. Lines 234-235: What statistical test was performed to test if the slopes were significantly different? ANCOVA?
Validity of the findings: The limitation of not knowing the length of time an athlete has played their sport, or the age in which they started the sport is a major one. However, it is appreciated that authors are aware of this and mention it in the Discussion. A larger sample size and analysis relative to sport would be a logical next step.
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: TIBIA FUNCTIONALITY AND DIVISION II FEMALE AND MALE COLLEGIATE ATHLETES FROM MULTIPLE SPORTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: 1. The terms used in this paper are very confusing.  "Functionality" is in the title, so I wanted to know what was meant by that.  Line 71 tells the reader that "The variability of robustness is associated with functional inequivalence" but inquivalence between what two things is not specified and no reference is given.  Line 73 seems to equate "bone size" (or possibly variation in bone size) with "robusticity" (are robustness and robusticity the same thing?). Line 74 seems to equate "strength" with "function".  Line 75 seemes to indicate that "slender" bones have "low robusticity".  On lines 82-83, it says that it is important to know if "bone strength is affected by robusticity (functional inequivalence)". Lines 195-197 state "Bone mechanical functionality is traditionally assessed by plotting a morphological bone trait (SSIp) against a measure of bone size."  Having clear definitions for all these terms would help the reader to understand the stated purpoise of the study that comes at the end of the Introduction.

2. The hypothesis doesn't make sense.  Lines 102-104 state "It was hypothesized that there would be a difference in bone strength and cortical area dependent on robusticity in Division II collegiate athletes."  One difference, or are two differences being hypothesized?  Is there a hypothesized difference in bone strength (or area) between two groups or conditions?  Or is it the case that a corrlation between strength (or area) and robusticity is being hypothesized?

3. The paragraph beginning on line 85 doesn't have a clear topic.  It starts off with a topic sentence about the effects of high-impact loading, then discusses variability in bone strength, then states the purpose of the study.  I suggest revising this paragraph to give it a clearer first sentence about variability and put the purpose and hypotheses in a separate paragraph.

4. The title needs attention. Should the "and" be "in"?
Experimental design: 1. How can we make comparisons between male and female athletes when these athletes played different sports?

2. When muscle strength and power measures are described in the Methods (starting line 127) it is not at all clear why these measures are relevant to the stated purpose of the study.
Validity of the findings: 1. I suggest rewriting your Results so that each paragraph begins with a clear statement of a key result.  Also, why is the formation of groups being described in the Results (line 240) and not in the Methods?  What your results suggest (line 269) and comparisons to the work of others (line 299) should be in the Discussion, not the Results.
Additional comments: 71-73: This sentence does not make sense - is there supposed to be a comma after "inequivalence"?

110: University students?

114: What is a "referent"?  I am not used to seeing this term in this context.

114: Why do some participants have "unknown" race or ethnic background?  How was this determined?

132: What is "Hammer Strength"?

143: What is a "Vertec"?  I know what this is, but you need to tell the reader.

153: Is "Absolute Peak Power" the same as "Peak Power" from line 151?

157: "dominant-side tibia"?

162: Is this the medial epicondyle of the tibia or the femur?  If it is the tibia, why is knee angle important?

168: "were"

184: What assurance do you have that the variables did not depend on which did the analysis?  Do the reported CVs address this, or just the within-technician precision?

331: Typo - "Wolff"


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: TIBIA FUNCTIONALITY AND DIVISION II FEMALE AND MALE COLLEGIATE ATHLETES FROM MULTIPLE SPORTS
Review round: 1
Reviewer: 3

Output:
Basic reporting: This manuscript is clearly written, well-structured, and references the most up-to-date studies that are relevant to the study. However, the 4% diaphyseal site was mentioned, outlined in the methods, but not reported. This would clearly be a welcomed addition to the data, as it provides a trabecular assessment, however it may be too much to include within this manuscript. Therefore, I suggest removing mention of this site from the paper. Also, two terms are used that are contentious and/or not well understand that you may want to consider changing; functional inequivalence and optimal/optimized/optimization.
Functional inequivalence is not well understand in the bone field and leads to much confusion among those unfamiliar with the term. You essentially could remove this term and not lose anything as you already state 'natural variation relative to robustness.' Optimal is very contentious in the bone field as it implies that under normal loading conditions one bone is better than another, when in fact, any bone that maintains its integrity is sufficient irrespective of any morphological/compositional differences. For this reason I would use a term such as 'adequate.'
Experimental design: This article meets all the criteria of an original, well-designed study. I have no comments.
Validity of the findings: Overall the findings are consistent with prior studies by others, and demonstrates that the concept of robustness holds up in a more extreme loading setting. Obviously it would be nice to know how these bones actually performed with some clinical measure of stress fracture incidences but this manuscript can stand alone, with hopefully a future study including clinical outcomes.
Additional comments: Overall this is a very nice study that expands prior work conducted using military recruits and cadaveric specimens. The authors provided adequate background, detailed methodologies, and did not over-interpret their results. Their findings are consistent with previously published work and is a welcomed contribution to the bone literature.


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: A SHORT, ROBUST BRAIN ACTIVATION CONTROL TASK OPTIMISED FOR PHARMACOLOGICAL FMRI STUDIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: See general comments
Experimental design: See general comments
Validity of the findings: See general comments
Additional comments: "A short, robust brain activation control task optimised for pharmacological fMRI studies" by Harvey et al. proposes a new standardized task fMRI paradigm optimized for short duration and ease of use. It has a potential for broad adoption in clinical studies.

Comments:
- Line 45: not clear what is the difference between “reliability coefficients for the tasks” and “Voxel-wise reliability metrics”. Maybe more intuitive labels could be used (ROI vs voxel)?

- I really enjoyed the outline of properties of a good pharmacological fMRI task. Maybe it would be good to highlight it in a box or a table. It makes a great guideline for future developments in this area.

- It might be beneficial to accompany the manuscript with video recordings of the visual and auditory stimuli of an example run for the two tasks. Such videos could be a great way to showcase the task to prospective users.

- It is not very clear how the instructions were delivered and if they are standardized. I could not find the instructions in the accompanied code. If this task is supposed to be broadly used in a clinical setting instructions should be explained better or automated.

- The manuscript would benefit from a figure describing the experimental paradigm.

- Why is the buffer time (10s) at the end rather than the beginning? Putting it at the beginning would help with potential non-steady state effects often found in EPI sequences.

- Line 175: missing comma after “31ms”

- Line 182: please specify which template was used

- Line 190: missing citation for ICC (TODO)

- Line 219: referencing figures is usually done with capitalized form (“Figures” vs. “figures”)

- Line 187: It seems that session effects were not modeled explicitly. It might be worth considering a model that removes session mean?

- Figures 1 and 2: I noticed that effects were tested and reported only in one direction (positive). This made me thinking – How would the negative effect look like? It would probably be task-negative network/default mode network. It might be worth looking at “any task vs null” contrast to see if this short protocol can also be used to reliably map that network.

- Figure 3: please consider drawing lines linking corresponding sessions 1 and 2 for each participant. You might also want to reconsider using yellow on white – it has poor contrast. (example: https://www.nature.com/articles/sdata201454/figures/3)

- Big kudos for sharing statistical maps on NeuroVault

- Line 364: It's great that authors share the code, but I don't think figshare is the best place to do it. Uploading the code to GitHub and using zendo for long-term preservation would allow users of this paradigm to submit improvements and bugfixes.

- Source code should specify all of the dependencies with their versions. This could be easily done with "pip list" or "conda list"

- Finally, I strongly encourage the authors to share the raw data from this study. This should be relatively easy on a dedicated platform such as https://OpenNeuro.org


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: A SHORT, ROBUST BRAIN ACTIVATION CONTROL TASK OPTIMISED FOR PHARMACOLOGICAL FMRI STUDIES
Review round: 1
Reviewer: 2

Output:
Basic reporting: Very well written and super clear manuscript.
Experimental design: The authors present a novel paradigm with a specific goal described of use in pharmacological imaging studies. In relation to previous studies that have used single tasks the logic is clear and the aims are good. As I understand the authors present the relatively straightforward idea that a short, multi component task and this leads to reliable activations across a variety of brain regions. By using this is a drug study then the LACK of effect on this task can be taken that the drug does not have non-specific vascular effects. This is an improvement on a small number of other studies (one is given as an example) that only tested a single modality in the control task.

There are two issues not address by the authors in presenting this framework. The first is that the fMRI tasks of interest in any study already include control conditions and therefore are intrinsically controlling for ‘non-specific’ effects of drugs. The authors need to articulate how an additional control task assists, for example drawing on the issues of task design and ‘controls of controls.’ The second issue is that the logic requires the control paradigm to show NO effect of the drug and therefore is subject to problems in statistical inference. What is the statistical framework in which the authors see this task being used? Bayesian, interaction effects, something else? A comment on its implementation would be welcome.

The description of the methods could be improved. Was there a training session? Was the paradigm sequential blocks of the different modalities or were they intermixed? If blocked, were they randonmised? Was the data analysed as blocks or event-series?
Validity of the findings: The data processing and analysis are otherwise clear. There are current changes in practice suggested by the literature that are not incorporated. Please justify why not, or instead consider updating the analysis. First, the movement appears to be modelled using only the six parameters (but this is not explicitly stated). Using up to 24 parameters is proving to be better in terms of reducing noise and preserving signal, as are other methods such as ICA-FIX/AROMA. Second, a cluster-forming threshold of z=3.1 is used. The well-known paper by Eklund et al. (www.pnas.org/cgi/doi/10.1073/pnas.1602413113) demonstrated that in FSL this gives elevated false positive rates of clusters. Please consider using different cluster-forming thresholds. Given the reliability output, using more than one threshold in FLAME could provide useful information.

For the ICC and Z maps the authors claim good overlap, but it is not clear what this is based on. Visual inspection? Proportions? Numerically indexing the overlap would be important as it is difficult to tell from the images alone, which contain substantial red and green (i.e. no-overlap) voxels. Does it matter that they overlap?
Additional comments: The manuscript would benefit from a table of coordinates for the peaks in activation and ICC clusters, including the extents.

The lower reliability in the eye-movement task is discussed in lines 324-329. Is it possible that another reason is the inclusion of error trials? It is not said what was done with these even though they were only 6 % of trials on average.

The availability of the task and data is a strength as good reliability data sets are few and far between.


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: GROWTH UNDER COLD CONDITIONS IN A WIDE PERENNIAL RYEGRASS PANEL IS UNDER TIGHT PHYSIOLOGICAL CONTROL
Review round: 1
Reviewer: 1

Output:
Basic reporting: Literature review on hormone signalling and gene expression during cold stress is fragmented and not relevant to the study conducted.
Experimental design: Description off the Material and methods is not sufficient. No indication how often chlorophyll content was measured. Authors state that dry weight of the plants was determined however no data provided and discussed.
Validity of the findings: The conclusion that growth under cold conditions is under tight genetic control is not validated by authors' findings. On contrary authors state that they could not see any variation in growth response amongst 57 accessions under cold conditions. Furthermore authors indicate that cell membrane damage occures at temperatures above 0 degrees Celcius by providing higher electrolyte leakage at day 70 compared to day 40. Increase in electrolyte leakage could also be a consequence of higher electrolyte accumulation at lower temperatures known as cold hardening.
Additional comments: The work presented provides a solid initial step for further in-depth analysis of genetic control of perennial ryegrass growth under low temperature conditions. However the manuscript presented in it's present form has major experimental flaws which should be addressed first.


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: GROWTH UNDER COLD CONDITIONS IN A WIDE PERENNIAL RYEGRASS PANEL IS UNDER TIGHT PHYSIOLOGICAL CONTROL
Review round: 1
Reviewer: 2

Output:
Basic reporting: The English Language is OK, but some sentences should be improved.

Literature, background, context:
The objectives stated at the end of the Introduction is: 1) to find out how much natural variation in cold tolerance (more precisely: chilling tolerance) there is in perennial ryegrass and 2) how growth characteristics vary between ambient vs chilling temperatures and in different genotypes. (comment: it is not genotypes, but populations, that are compared). The growth characteristics studied are shoot biomass accumulation (above 4 cm), leaf elongation, chlorophyll content and electrolyte leakage (i.e. not only growth characteristics).

The background is that with climate change it is a goal to breed for varieties that better utilize the extended growing season. In this respect it is relevant to refer to Ergon, Agronomy Journal, 2017 (Optimal Regulation of the Balance between Productivity and Overwintering of Perennial Grasses in a Warmer Climate). Is there no probability of freezing damage or chilling damage if Growth starts to early in spring under Irish conditions? Maybe not, but I miss a judgement of that.  There is interesting and relevant information in the Introduction, but it seems a bit disconnected from the objective of the study, the experiment and the results. The introduction describes some processes relevant for cold acclimation, but this is not considered much further in the manuscript, which focusses on Growth and stress symptoms at chilling temperatures.  Did you do a literature search on "(perennial ryegrass) AND (low temperature)"? I suspect you would find more literature that is more specifically related to Your study and objectives. I also think there is more relevant literature on Growth models for perennial ryegrass.

The results are not sufficiently discussed in relation to other scientific literature. Only very few References are mentioned in the Results&Discussion, and there they are mostly presented as statements, without being linked properly to the discussion of the presented results.

Structure
Results and Discussion is combined into one Chapter, unlike the recommendation from PeerJ.

Results vs hypotheses/objective
The results and objectives fit together - The (lack of ) variation in Growth at low positive temperatures is shown, and the effect of low positive termperatures on growth and stress symptoms is characterized. This is what the paper should focus more on, both in the title, introduction, and discussion.
Experimental design: No comment, seems OK
Validity of the findings: Results from Statistical analysis is not reported in a satisfactory way. I would like to see tables With degrees of freedom, significance Levels etc. Would it be better to do an ANOVA With Population, treatment and the interaction between these?

I am Critical to the title, and the conclusion that growth under Cold conditions are under "tight Genetic Control". First of all, I am not sure what this is supposed to mean, but to me it indicates that Genetic Control is more important than environmental Control. I think the results shows the opposite: there is environmental Control, but no Genetic variation. The proposed idea of selecting for improved Growth under warm pulses is interesting and relevant, although the Reference to Brereton and McGilloway appears a bit far-fetched, and had better been placed in the discussion before conclusions. The rest of the cocnluding paragraph should also be moved out of the conclusions, and the conclusions should rather focus on answering to the objective of the study.
Additional comments: State if you are using forage cultivars, lawn cultivars, or both.

I think the results are interesting, but the paper is too immature, and not sufficiently focussed yet.


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: GROWTH UNDER COLD CONDITIONS IN A WIDE PERENNIAL RYEGRASS PANEL IS UNDER TIGHT PHYSIOLOGICAL CONTROL
Review round: 1
Reviewer: 3

Output:
Basic reporting: The mansucript is interesting but not well written and the message poorly packaged.

The authors should be encouraged to improve the English - many sensences are complex with the sub-clauses often in the wrong place for ease of comprehension.

The major problem, in my opinion, is that the results are presented as if they dont mean much.   The authors *may* have found evidence for a differential brake on growth but their dataset is not sufficient to allow them to make this claim.  For this they would need to collect data for at least some strains at intermediate temperatures; alternatively, they should review their existing data in the light of current ambient temperature literature and gibberellin literature, and critically revise the hypotheses that could be then generated.   They could also suggest  how they could improve or extend their current expts tto test those hypotheses.

there is significant mechanistic understanding (and gaps) in terms both of ambient temperature response and in growth arrest due to stress from model systems such as Arabidopsis and rice.  Given the general conservation of mechanism across the tree of life, it would seem very likely that these pathways would be very highly conserved in flowering plants.
Experimental design: A key problem is that they have  tested only 2 temperatures.  its probably not feasible, nor fair , to ask for more in this report.  However, there is no serious discussion of how the study could be extended to address this - and also explain clearly and concisely why it is necessary.  Such discussion should be added.
Validity of the findings: they seem fine - in so far as they go.
Additional comments: The response you report in interesting but by not relating it well to the current thinking on growth arrest under stress, you under-sell the story.

Conversely, the title of the paper seems to over-claim. Based on the current data, i dont think you can make the statement "under tight genetic control".  While i'd like to think you are correct, and you might be, you've only tsted a small number of environments and you dont provide an indication of what the genetic mechanisms are or even might be.


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: GROWTH UNDER COLD CONDITIONS IN A WIDE PERENNIAL RYEGRASS PANEL IS UNDER TIGHT PHYSIOLOGICAL CONTROL
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Authors have taken efforts to address the areas of concern and have substantially improved 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: A COMPARISON OF PERCEPTIONS OF NUTS BETWEEN THE GENERAL PUBLIC, DIETITIANS, GENERAL PRACTITIONERS, AND NURSES
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The manuscript is very well written and Informative. I’d like to thank the authors for all the work they’ve put into it. Some minor comments and suggestions for improvements are below:
INTRODUCTION
Lines 77-84: The suggestion that individuals would increase nut intake if advised by doctor seems to be in contrast to the findings discussed from these studies. Please modify sentences 77 to 78 to reflect the discussion in 78-84.
METHODS
Lines 121, 123: Please state once that the questionnaires used multiple response questions so you don’t need to state it repeatedly.
Lines 142-143: How was this enforced with paper questionnaires?
Lines 156-157: Please state what tests specifically were used. What kind of chi-squared tests, linear regression models?
RESULTS:
General comments: Please show P-value<0.05 whereever significance is mentioned in results section and what effect was significant.
Line 168: Where does the N=1440 come from. It seems like this number should be much lower? Please double check.
Line 200 and other places: Please be consistent with showing the N for all %s.
Lines 205-208: Where is this data shown in Table 3?
Line 216-: Suggest arranging the perception and knowledge of nuts results section so that the strongly agree to strongly disagree results are discussed first and then the ‘I do not know’ results for clarity.
Lines 233-238: Could you show % ranges like shown in the previous paragraph regarding what % agreed, %disagreed?
DISCUSSION
General comments: The results seem to be reiterated in the discussion. The discussion section could be refined further by discussing the implications of the important findings only.
Lines 251, 257: The term ‘significant differences’ with respect to results doesn’t need to be mentioned in the discussion
Lines 265-272: The discussion of the Pawlak et al studies is repetitive. Suggest removing the discussion from the introduction and elaborating it in the discussion only.
Line 364: In addition to Sabate et al 2010, suggest citing a recent review i.e. “The effects of almond consumption on fasting blood lipid levels:a systematic review and meta-analysis of randomised controlled trials”


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: A COMPARISON OF PERCEPTIONS OF NUTS BETWEEN THE GENERAL PUBLIC, DIETITIANS, GENERAL PRACTITIONERS, AND NURSES
Review round: 1
Reviewer: 2

Output:
Basic reporting: Good English, appropriate references, well structured and with apparently relevant results
Experimental design: This is not really original research The authors have carried out a moderately large survey amongst health professionals and the general public about beliefs, perceptions and obstacles concerning nut consumption. Unfortunately, they have chosen to slice salamy-style the results and have already published three papers providing somewhat different views of the results. Two of these papers are just cited for the methodology (Brown et al 2017 and Yong et al 2017) and another (Brown RC, Gray AR, Yong LC, Chisholm A, Leong SL, Tey SL. Current nut recommendation practices differ between health professionals in New Zealand. Public Health Nutr. 2018 Apr;21(6):1065-1074. doi: 10.1017/S1368980017003469. Epub 2017 Dec 4.) not cited even though it was published online a while before the present manuscript was sent for publication. Interestingly, these latter paper has the same authors and they are listed in the same order as in the present manuscript.

Thus, this research is far from original and, worse, authors have deliberately omitted citing prior published work that compromises the present one.
Validity of the findings: As per point 2, the findings are invalid.
Additional comments: This article is flawed because most results have already been published, as per the two references cited (brown 2017 and Yong 2017) and another one with exactly the same authors and in the same order has been omitted (Brown RC, Gray AR, Yong LC, Chisholm A, Leong SL, Tey SL. Current nut recommendation practices differ between health professionals in New Zealand. Public Health Nutr. 2018 Apr;21(6):1065-1074. doi: 10.1017/S1368980017003469. Epub 2017 Dec 4). This kind of slicing results of a single investigation is not scientifically sound.


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: A COMPARISON OF PERCEPTIONS OF NUTS BETWEEN THE GENERAL PUBLIC, DIETITIANS, GENERAL PRACTITIONERS, AND NURSES
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Thank you for revising the manuscript. It is much 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: A COMPARISON OF PERCEPTIONS OF NUTS BETWEEN THE GENERAL PUBLIC, DIETITIANS, GENERAL PRACTITIONERS, AND NURSES
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The presentation of the article is overall good. I feel there is a lack of information regarding other human-health related effects of nuts and the possible molecular mechanisms underlying such effects. Looking at the flow of the paper I believe this part would fit introduction section. Accordingly, please add the following paragraph in the introduction:

Nut consumption has been associated with reduced risk of certain cancers, such as colorectal, endometrial, and pancreatic neoplasms. Evidence regarding nut consumption and neurological or psychiatric disorders is scarce, nonetheless a number of studies indicated significant protective effects against depression, mild cognitive disorders and Alzheimer’s disease. Several molecular mechanisms appear to be implicated in the protective role of nuts, including antioxidant and anti-inflammatory properties, mainly related to their high content in mono- and polyunsaturated fatty acids (PMID: 26586104).


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: MEASUREMENT MATTERS: HIGHER WAIST-TO-HIP RATIO BUT NOT BODY MASS INDEX IS ASSOCIATED WITH DEFICITS IN EXECUTIVE FUNCTIONS AND EPISODIC MEMORY
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: The biggest shortcoming of the study was that BMI was calculated by participants’ self-reported weight and height. This may be one of the reasons that there was no relationship between BMI and cognitive outcomes (EF and episodic memory).

In addition, please clarify more details of the methods of measuring WHR.
Who measured the WHR of the participants?
Validity of the findings: Another major concern is the effect of multicollinearity.
Please provide the variance inflation factor (VIF).

I recommend adding scatter plot of main results.

In addition, why did authors not conduct moderation analyses that examine whether the relationship of obesity to EF and episodic memory could be moderated by sex?
I recommend the moderation analyses for the following reasons.
1.	Gender differences in the regulation of body-weight are well documented.
2.	Sex may be a biological variable that related to cognitive decline (e.g., Sohn et al., 2018, Scientific Reports).
3.	Males and females differ in adipose tissue distribution and expansion (Zore et al., 2018, Molecular Metabolism, for a review).
Additional comments: No additional comments