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: NIGHT OF THE HUNTER: USING CAMERAS TO QUANTIFY NOCTURNAL ACTIVITY IN DESERT SPIDERS
Review round: 1
Reviewer: 1

Output:
Basic reporting: I really like this paper, it is clear, well laid out and will be of significant interest to the entomological community (where the use camera traps to observe invertebrates have long been dreamt of!)
The background is well researched and the study is well placed in the Simpson dessert as it presents an interesting proof of concept for the camera traps and utilises relevant environmental variation (eg. responses to fire, which is a "hot" topic in Australia at the moment).

Specific comments

Intro:
•	L62: if you want a reference on the importance and use of invertebrate trait data for international comparisons Wong M.K.L., B. Guénard & O.T. Lewis 2019. Trait-based ecology of terrestrial arthropods. Biological Reviews 94:999-1022. doi:10.1111/brv.12488
•	L64. Instead of destructive like this to be more clear. Eg. Usually result in the death of the individuals captured

Methods:
•	Please include a section in the methods on how you identified lycosid spiders from other similar spiders in both the spotlighting and the images

Figures:
•	Not sure why there are two figure captions for the figures? I guess this is a result of the manuscript input forms
•	Figure 1: can you add burned unburned labels to the figure?
•	Figure 1 legend, the current wording is a little confusing. consider rephrasing to: Two camera positions were tested: a) angled at 45 degrees (orange squares n=6) etc.
•	Figure 3: is there any way to make the frequency observation axis more clear? You need to add % to the axis too, as in Figure 4. It’s a bit unclear why axis has the points 3.75 and 7.5 rather than regular the points on other figures (same for a in Figure 4). If they were all the same eg. 5%, 10%, 15%, 20% it would be easier to make comparisons. Figure 5 looks great on all these points, just make Figure 3 and 4 conform to the same details.

Discussion:

I'd like to see mention of the other data that can be collected from camera traps. Specifically useful trait data. One of the interesting life history traits of wolf spiders is that they carry their offspring on their backs. Was there any way of detecting this in the photos? This would provide additional (and very useful) data (eg could study differences in reproductive cycles in different areas or boom bust cycles). I’d also like a discussion of what types of trait data eg. Size, maybe even speed or activity could be collected from the photos.

The discussion seems to focus mainly on the differences in activity patterns, but the number of spiders detected (eg. The number of photos) deserves some discussion  too (eg paragraph 3 on dune vs crest activity, where there was a difference in number of individuals detected, but no difference in activity patterns).
Experimental design: The experimental set up is good, and I like that it addresses two different types of environmental variation (the location on the dune and the time since fire).

I also think that the comparison between the spotlight data and the camera trap data is useful, despite the limitations (which are well covered in the discussion).
Validity of the findings: I might have misunderstood here, but if the lycosids were only found in the time laps, and you didn’t use the time laps during the day then I don’t think you can make the claim that Lysocids are only nocturnal. Same problem with the spotlighting, unless you also did transects during the day you cant make the claim they weren’t active then. In other habitats lycosids are known to be quite active during the day.

Desert habitats are great in that they have nice open spaces in which to face a camera and get a good contrast of the spider against the sand. You mentioned this briefly in the discussion, but could you comment more on how you think this method would work in different ecosystems? Eg. Against a forest floor or in grasses? I think this might be a large limitation.
Additional comments: I like your coverage of the limitations, but of course, there are many. My thoughts below:

What do you think the potential is for biodiversity studies? You may not have this data, but it would be interesting to know the other invertebrate fauna that were also detected (this could widen the scope of the paper to appeal to other invertebrate researchers). Eg. Did any invertebrates trigger the motion capture? This has been the main problem in using this method in the past.

What do you think of the possibility of using baiting the stations (eg tethered prey like meal worms) to attract arthropod predators?


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: NIGHT OF THE HUNTER: USING CAMERAS TO QUANTIFY NOCTURNAL ACTIVITY IN DESERT SPIDERS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The dataset reported here does not appear to be "self-contained."

I took a look at Potter et al. 2018 (https://royalsocietypublishing.org/doi/10.1098/rsos.171872) because I was interested in seeing how the two Lycosa species had been identified and this paper was referenced in line 144. Upon closer examination I found that the dataset reported in the manuscript currently under review in PeerJ has already been published in Royal Society Open Science as part of a paper investigating space use and activity by wolf spiders and dunnarts.

The current paper clearly has a different goal and adds some additional analyses to the findings already reported in Potter et al. 2018, but nowhere in the manuscript is it mentioned that these data have already been published elsewhere. Rather, the current paper is written as if the data were collected specifically to ask the questions (1-3) stated in the abstract, rather than reporting that these data were collected as part of a larger study that used camera traps to detect dunnarts and spiders, and this is seriously misleading.

I have attached copies of the pdfs of the manuscript under review and Potter et al. 2018, in which identical or near-identical text from the methods and results section are highlighted. Figure 2 is identical to Figure 1A in the supplementary material of Potter et al. 2018, and Figure 3b. is indentical to figure 2Ab (https://royalsocietypublishing.org/doi/suppl/10.1098/rsos.171872). This is also an issue of self-plagiarism.
Experimental design: Please be explicit that the cameras were deployed and data collected as part of a broader study.
Validity of the findings: In lines 165-166 the authors state that “To ensure independence, multiple photographs likely to be of the same individual (photographs in sequence <2 min apart) were removed prior to analysis (Greenville et al. 2014; Heavener et al. 2014).”

This method of determining independence is seriously flawed.

First, this threshold appears to be based on one used by Greenville et al. for dingoes, and the other cited paper was on rats. These are mammals that trigger camera traps and no doubt two minutes makes sense for these animals.

A study which used camera traps to study spiders and other arthropods (Collett & Fisher 2017; https://onlinelibrary.wiley.com/doi/pdf/10.1002/ece3.3275), on the other hand, found that individual arthropods captured in successive frames of time lapse images stayed in the frame for a mean of 32 +/- 13 min, and that one spider remained in view of a camera for over 15 h.

The current paper found that spiders never triggered motion sensing on the camera traps, but rather spiders were only ever captured in time lapse photographs. These photos were taken every 5 minutes (lines 135-136) so by definition no photographs of spiders can be excluded because they are <2 min apart.

When one examines the raw data submitted with this paper, it becomes clear that a large number of presumed independent photographs of spiders are successive frames taken at 5 min intervals. For instance, in the first 36 lines of data, there are 4 successive frames from 22:20-22:35 on 2016-07-18, 27 successive frames from 4:35-6:55 on 2016-09-01, and 5 successive frames from 6:35-6:55 on 2016-09-03.

It seems much more likely that these 36 images (used as independent data points in analysis) represent three unique individuals rather than 36. Since the raw image data are not included with this submission I cannot check whether successive images appear to contain the same species or same individual, or how much the spiders move from frame to frame. However, given what I know about the ecology and behaviour of wolf spiders (they frequently remain still while hunting in a relatively small area, and also see Collett & Fisher 2017, mentioned above) it seems much more likely that the same individuals were frequently photographed multiple times rather than new individuals happening to enter the frame approximately every five minutes. Indeed, it seems incredible to me that a single camera (camera 1) deployed on 7 July detected no spiders until 18 July, then detected 4 spiders in rapid succession, then no spiders until 1 September, and 27 spiders in a row on that night, and then 5 spiders two nights later.

If these likely repeated records of the same individuals were taken into account in analyses this would not be a fatal flaw, but as the manuscript currently stands this is a major issue.
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: NIGHT OF THE HUNTER: USING CAMERAS TO QUANTIFY NOCTURNAL ACTIVITY IN DESERT SPIDERS
Review round: 2
Reviewer: 1

Output:
Basic reporting: I've had a good read through the rebuttal and the new manuscript. The authors did a very good job of addressing all of my comments and the paper reads really well now.
Experimental design: I'm happy with the responses the authors have made to previous methodological concerns.
Validity of the findings: no comment
Additional comments: This is a valuable contribution to the literature and reads very well, nice work


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: NIGHT OF THE HUNTER: USING CAMERAS TO QUANTIFY NOCTURNAL ACTIVITY IN DESERT SPIDERS
Review round: 2
Reviewer: 2

Output:
Basic reporting: I have only one comment:

Please describe how you identified the spiders to the genus Lycosa (cite key used, for example—I could not find any such reference in the previous paper about this dataset) and whether voucher specimens have been deposited in a museum collection (if they have not been, please do so, so that future researchers can verify the identification and benefit from the knowledge of which taxa are present at the study site).
Experimental design: Good.
Validity of the findings: Good.
Additional comments: This is an interesting paper containing valuable data and I enjoyed reading the updated version. I thank the authors for their efforts to deal with my comments and those of the other reviewers.

Besides the addition of reference(s) for the spider identification and information about voucher specimens above, I have only one other comment:

Why are the circular data displayed differently from figure 4 in figures 6 and 7? Either way seems fine but the latter two don’t seem to indicate the mean and consistent data display would be preferable.

I think that the manuscript is very clear and much improved based on the revisions, and is a valuable contribution.


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: TLR4 PROMOTER RS1927914 VARIANT CONTRIBUTES TO THE SUSCEPTIBILITY OF ESOPHAGEAL SQUAMOUS CELL CARCINOMA IN THE CHINESE POPULATION
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript meets the basic criteria of reporting.
Experimental design: The experimental setup is sound and reasonable. The methods are described in details (with a few exceptions; see specific comments) and all the relevant details are provided for data transparency and reproducibility.
Validity of the findings: The findings are novel and would benefit the field.
Additional comments: The manuscript submitted by Li and colleagues, presents analytical study on the association between genetic variations (SNPs) in the Toll-like receptor 4 (TLR4) and the risk of esophageal squamous cell carcinoma (ESCC) by employing case-control research strategy. Authors provide evidence supporting that TLR4 rs1927914 variant contributes to the ESCC risk possibly by alterations in regulation of the promoter activity. Although the manuscript describes some interesting findings; there are some limitations in its current version. Here are my specific comments that may help authors to improve the quality of the manuscript.

1) Authors claim that rs1927914 G allele was associated with elevated transcriptional activity. But the experimental biochemical evidence to support this claim is missing. Can authors provide any evidence on DNA binding activity of the nuclear protein factors to these alleles suggesting differential binding pattern?
2) A schematic showing TLR4 locus with SNPs investigated in this study would help. Also, authors may use this to explain the cloning strategy used to generate luciferase reporters.
3) Line 161-162: Authors write – “Table 2 showed the association of TLR4 rs1927914, rs11536891 and rs7873784 genotypes with the susceptibility to esophageal cancer”. But the Table 2 does not have any data for rs7873784. This need correction.
4) Lines 168-170: Authors write – “After genotyping TLR4 rs7873784 (G>C) and rs11536891 (T>C)… conforms to complete genetic linkage.” These results are not citing the relevant table/s.
5) Can the authors provide an evidence [or comment] on the specificity of Allele-specific TaqMAN genotyping probes?
6) Authors used TRANSFAC program for transcription factor binding capability. The results of this analysis are not shown or discussed. Also, authors need to cite the relevant references (is it PMID: 8594589?).
7) Same applies to microRNA binding ability prediction using ‘Web Server’(lines 102-103). Which ‘web server’ was used? Please cite relevant references. Also, the results are neither shown nor discussed.
8) Authors may need to include more literature on the SNPs and their association with disease. Also, the section described in lines 78-81 needs relevant citations.
9) In the conclusion section (which is very short), authors may add a note on the future prospect of this study, how does this study help in advancement in the current field.
10) Grammar check would help e.g. Line 216: “…be polyadenylation at 3’UTR..” should read “…be polyadenylated at 3’UTR…”
11) Table 4 is actually a figure. Please correct this. The legend needs to be added for this one. Explain how was the normalization done? Also, please correct the Y axis label. “Realitive” should read “Relative”.


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: TLR4 PROMOTER RS1927914 VARIANT CONTRIBUTES TO THE SUSCEPTIBILITY OF ESOPHAGEAL SQUAMOUS CELL CARCINOMA IN THE CHINESE POPULATION
Review round: 1
Reviewer: 2

Output:
Basic reporting: In the study by Li et al., evaluated the association of TLR4 polymorphisms with the genetic susceptibility to esophageal squamous cell carcinoma. The authors identify that the TLR4 promoter variant ‘ rs1927914’  that confer susceptibility to esophageal squamous cell carcinoma in Chinese population.

The objectives of the study are well defined and the authors provide reasonable findings to support the hypothesis.
The literature is well referenced and relevant to the study
The overall manuscript is well written, data presented is clear, conclusions are well drawn, and provides a new research finding on TLR4 polymorphism and susceptibility to ESCC.
Experimental design: In general experimental approaches are well designed with relevant controls, and appropriate statistics is included.

Some minor changes/modifications suggested as follows:
1)	Line #99 (Materials-methods section), authors mention of the criteria sought to select SNPs in TLR4 promoter. This description needs to be more clarified. Authors should provide rationale for the analysis of transcription factor binding on TLR4 promoter by TRANSFAC. Which transcription factor(s) binding to TLR promoter were analyzed?
(2)	Does the SNP in the TLR4 promoter, affect the binding of any known transcription factor?
(3)	Line #220, in discussion section, authors mention “Therefore, reasonable inhibition of TLR4 gene expression is conducive to disease recovery…”. This sentence needs to be modified, as inhibition of a single gene may not be sufficient for the disease recovery.
Validity of the findings: The data presented and findings from the study are appropriately given and conclusions are well drawn.
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: TLR4 PROMOTER RS1927914 VARIANT CONTRIBUTES TO THE SUSCEPTIBILITY OF ESOPHAGEAL SQUAMOUS CELL CARCINOMA IN THE CHINESE POPULATION
Review round: 2
Reviewer: 1

Output:
Basic reporting: Manuscript meets basic criteria of publication.
Experimental design: Valid experimental design and detailed description of procedures.
Validity of the findings: Manuscript provides insightful findings pertaining to esophageal squamous cell carcinoma biology.
Additional comments: Authors have addressed my comments successfully. The revised manuscript is scientifically improved and is now suitable for publication. I have only one minor suggestion. It would be helpful (for general understanding) to add an arrow pointing at the DNA-protein complex in Figure 1C (since there is no clear intact band).


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: TLR4 PROMOTER RS1927914 VARIANT CONTRIBUTES TO THE SUSCEPTIBILITY OF ESOPHAGEAL SQUAMOUS CELL CARCINOMA IN THE CHINESE POPULATION
Review round: 2
Reviewer: 2

Output:
Basic reporting: This study aims to analyze the association of potential functional genetic polymorphisms in TLR4 with the risk of esophageal cancer.
Experimental design: Well defined, and organized.
Validity of the findings: Authors addressed the required concerns in the revised version of the manuscript.
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: UNEXPECTED MITOCHONDRIAL LINEAGE DIVERSITY WITHIN THE GENUS ALONELLA SARS, 1862 (CRUSTACEA: CLADOCERA) ACROSS THE NORTHERN HEMISPHERE
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript by Neretina et al. provides first larger-scale data on genetic diversity of the smallest water flea in the world, highlighting its substantial unrecognized diversity. The dataset is very valuable, the results are novel and to the body of evidence about the real diversity and biogeographic patterns in freshwater zooplankton and cladocerans in particular. The manuscript is certainly worth publishing, though I believe some revisions are either needed or at least recommendable before acceptance (see below, and the annotated PDF).
Experimental design: The study is based on material from many parts of the world available to the authors, the molecular analyses focus on genes for which some reference data are available, and they are rigorously analyzed, though I have a feeling that some analyses are in fact unnecessary.
In some sections, the manuscript is too detailed. This is particularly true for the Methods – some details about the molecular analyses are trivial and may be omitted (but elsewhere some extra information is needed), and the data analysis is described in extreme detail. The authors have used many different methods but in some cases I believe the additional analyses do not provide any added value.
In fact, I totally fail to understand why the “Population analysis” section is included – the dataset is not particularly suitable for population-level analyses or consideration of past demographic changes, these analyses are not necessary for delivering the message, nor are appropriately discussed. Furthermore, the authors may consider removing some species delimitation methods (in particular those that tend to result in over-splitting, as is discussed in the manuscript; sticking to methods that tend to be conservative might be sufficient for this particular story).
Presenting the results in the form of network seems also unnecessary, considering the high divergence of the individual clades (and thus uncertainty associated with exact network topology). The biogeographic patterns may be easily shown on the trees if the origin is highlighted by colours.
Overall, I believe the number of figures in the supplement may be reduced, some descriptive data in tables may not be necessary, and the Table 3 would rather fit to supplement.
Validity of the findings: The main conclusions are clear, and discussed appropriately. Sometimes, however, I feel the authors discuss even aspects or concepts that are not needed (e.g., focusing on an approach suggested in obsolete papers, or discussing in length the problems of subgeneric splitting without explaining why we need such splitting in the first place). Some of the aspects of biogeography or endemism seem to me overinterpreted, though, considering the limitations of the dataset. I point out to these specific issues in the annotated PDF.
I was not convinced by the level of splitting of the Alonella clades that are indicated in the trees and discussed in the main text. In some cases, the splitting to subclades does not seem to me as supported by the data on either gene (see, e.g., C1 vs C2, or D3 vs. the rest of the D clade). I do not think these subclades are in fact needed to describe or interpret the resulting patterns, so I urge the authors to very carefully consider when such subdivision is really warranted.
Discussion might also benefit from some restructuring. Especially at the beginning, it should be stronger, highlighting the main findings. The present version starts with explaining what pseudogenes are, which seems to me unnecessary.
Additional comments: I am providing rather detailed annotations to the main PDF (including comments to figures and tables), which I urge the authors to consider carefully. These deal with various aspects, both conceptual (requesting clarifications, improving visualization, commenting on particular conclusions) and minor (correcting inappropriate statements, rewording suggestions, etc.)
In general, despite specific comments and occasional criticisms, I like the story and look forward to seeing it published in the near future.


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: UNEXPECTED MITOCHONDRIAL LINEAGE DIVERSITY WITHIN THE GENUS ALONELLA SARS, 1862 (CRUSTACEA: CLADOCERA) ACROSS THE NORTHERN HEMISPHERE
Review round: 1
Reviewer: 2

Output:
Basic reporting: This paper provides molecular evidence for cryptic diversity within three species of Alonella in the Holarctic. The conclusions are solid as far as they go, being founded on a quite comprehensive suite of phylogenetic analyses based on two mitochondrial gene regions. Although the geographic coverage is wide, the sampling is sparse for many regions (particularly North America). Alonella excisa is the most diverse among the three morphospecies studied, as would already be expected from public data in the BOLD database. The genetic distances found among clades strongly suggest that they are in fact good species, although further studies (including nuclear markers as well as morphology) are needed to corroborate this. The authors also document clear geographic structure in the distribution of clades, which again supports the distinctness of the various clades.
The analyses conducted are diverse and elaborate, following much the same approach used in a recent paper published by partly the same group (Sinev et al 2020, Zootaxa 4767 (1): 115–137). I get the impression that the elaborate analyses make something of an overkill on this limited dataset, but then I am not familiar with all the approaches applied. The results from different analyses are congruent and convincing enough. Nonetheless, I believe the general phylogenetic picture presented may have to be modified when sequences from more regions are added. It seems particularly important to include more samples from the Nearctic. This is further underlined by the author’s conclusion that clade K is basic to all other Alonella taxa. Still, the present paper is a significant step on the way to a more complete picture, and is therefore welcome.
I have no major objections to raise. I find the text unnecessarily long and wordy, but realize that both writing in English as well as tradition may contribute to this. In the following I point out a few issues that I recommend be addressed.

Methods: The heading “Population analysis” seems misleading, since no analysis of population structure is presented. Rather, the stated issue is on measures to avoid potential influence of population structure on the phylogenetic reconstructions. The various indices referred to here were calculated for clades, not for populations. I suggest simply to remove the heading.

Results: The authors should provide information on fragment lengths, alignment lengths and gaps in the alignments. In Table 1, the column called “n” provides # of sites without gaps, which is something else. I also wonder why the number of sites given for COI are unexpectedly low - the primer set they applied normally yield >650 bp, also in the three Alonella morphospecies. This may be due to poor quality of some sequences, but should in any case be commented on. I also miss information on checking for stop codons in the sequences.

Discussion: Some of the biogeographic/historical explanations suggested may be premature, but I have no objection to have them included. Comparisons with similar patterns in other species are certainly of interest.

Figure 4, legend: Information on which marker (16S) which the clades are based on should be included (at least some of them are only based on 16S).
Figure 5, legend: Statements about coloration are unclear. Two shades of grey are visible, I suggest “Dark grey” and “Light grey” to make clear the meaning.
Tables 1 and 2: Please include information of what the “other” groups are.

Details and minor issues
L. 126: manufacturer’s instruction – which manufacturer?
L. 158-159: Somewhat weird sentence (first part) – I suggest «The most appropriate substitution models and partitioning schemes were found via ModelFinder …»
L. 198: Instead of «similar what allows» I suggest «similar, which allowed»
L. 236: Write “according to Reid & Carstens”
L. 238 & 239: Substitute “which” for “what”
L- 248-252: This sentence is both complicated and incomplete, please rephrase
L: 266: Substitute “had” for “have”
L. 267: Delete “was”
L. 310: write “unsuccessful PCRs”, and delete “are”
L. 318-319: I agree that grouping the animals into morphotypes is reasonable, but the statement seems superfluous here. The reference to tables 1 and 2 appears illogical, since they present only DNA results. I believe what you mean is that the molecular results support the initial grouping based on morphotypes. If so, this should be stated clearly.
L. 321: The G+C content refers to the DNA sequence, not the translated amino acid chain. I suppose what you mean is the coding COI locus.
L. 366: From Table 3, I found the range of p-distances is 12.1-25.1 % for COI, and 10.6-27.2 for 16S. I suggest you specify these values separately for each locus in the text here.
L374: Write “the same major clades in both mitochondrial loci”
L. 389: Substitute “which” for “what”
L. 402: “relatively accurately” is an unfortunate expression. Relative to what? There is no mention of stop codons or pseudogenes in the Methods or Results sections, and such information should be provided. Phylogenetic reconstructions can be influenced by many other factors including geographic sampling, selection of genetic markers, etc. My guess is that this mitochondrial phylogeny will be modified in the future particularly by expanding the geographic coverage.
L: 423-424: The expression “just add water” is obscure and should be avoided. Be more specific in this criticism
L. 428: Last word should be “applications” (plural)
L. 458: replace “meanwhile” with “while”
L. 462-463: “Exclusively Nearctic taxa are found within many taxa” just sounds odd – maybe replace the first “taxa” with “clades”?
L. 469: I suggest “An example” instead of “The example”
L. 482: “TYA” = thousand years ago? Better spell it out
Experimental design: Research aims are clearly stated and appropriate. This work is empirical rather than experimental, and the authors have drawn on the material and data available to them. As stated earlier, the analyses are elaborate and include several quite recently developed tools, and the results are convincing.
Validity of the findings: As previously stated, the conclusions are convincing. Speculations on biogeographic history and possible dispersal routes are relevant and acceptable.
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: UNEXPECTED MITOCHONDRIAL LINEAGE DIVERSITY WITHIN THE GENUS ALONELLA SARS, 1862 (CRUSTACEA: CLADOCERA) ACROSS THE NORTHERN HEMISPHERE
Review round: 2
Reviewer: 1

Output:
Basic reporting: The revised manuscript has improved in most aspects, and while I still agree with the other referees that some of the thorough analyses may be a bit of an "overkill", considering the very clear patterns observed, there are only a few minor issues that need to be clarified or corrected before acceptance.
Experimental design: No further comment.
Validity of the findings: Perfectly adequate.
Additional comments: I am generally happy with the way how the manuscript was improved by the authors. In the annotated file provided along with the review, I have included various corrections, suggestions for rephrasing (sometimes, I believe rephrasing is necessary to avoid confusion or ambiguities), and requests for clarification. These are in the form of either comments or tracked changes, and I believe the authors will have no problem with dealing with them.

In most cases, when the authors did not agree with my previous comments, I accept their decision. However, I believe the opening of the discussion ("Based on a logics of the "standard screening threshold of sequence difference (10× average intraspecific difference") (Hebert et al., 2004), we would have to conclude that each the excisa, exigua and nana is represented by a single polymorphic species. ") is based on an outdated concept, and thus not suitable. The assumption that interspecific divergence should be 10x the intraspecific one, is not warranted - I see no reason why to disprove all the outdated concepts that have emerged sometimes in the past. I strongly suggest the authors skip this bit - it is like a breaking into a widely opened door...

In addtition to the issues in the annotated manuscript, I would like to highlight the need for a careful check of the supplementary information.
In the Supplementary table 1, there are some lines where neither COI nor 16S accession number is provided (but apparenlty the sequences were available, as the clades and subclades are indicated). They need to be filled in. There are also two empty sheets ("list", labelled in Russion) that are not necessary.

In the Supplementary table 2, at least rough coordinates for the Danish site might be provided. I also suggest that the authors include columns for GenBank and/or BOLD acc. no., so the potential users of this information do not have to extract them manually from the code column.
In fact, I believe both of the above-mentioned supplementary tables may be easily merged into one, which would make the work with the data much easier.

The Supplementary Table 3 is in the Word format, spanning multiple pages, and difficult to read. It would be better to provide it in a spreadsheet form as well.


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: UNEXPECTED MITOCHONDRIAL LINEAGE DIVERSITY WITHIN THE GENUS ALONELLA SARS, 1862 (CRUSTACEA: CLADOCERA) ACROSS THE NORTHERN HEMISPHERE
Review round: 2
Reviewer: 2

Output:
Basic reporting: I reviewed a previous version of this manuscript earlier. Many of the comments I made then were intended to aid the authors in improving the language. While their response letter states that they have made corrections accordingly, this is not always the case. So, I recommend the authors to look through the previous suggestions again.

I still find the long and complex treatment of delimitation of putative species an overkill. The methods, results and discussion related to species delimitation make up a large fraction of the paper. Since the authors seem to insist on keeping this elaborate element, at least they should provide some statement of their motivation for including so many approaches that yield similar results. One of their conclusions is that missing data on one mitochondrial locus can be remedied by data on another mitochondrial locus (lines 397-398). In my opinion, their data do not allow for this conclusion, which must be based on analyzing a complete dataset (without ‘gaps’) for comparison with the incomplete alternative.  While the results on delimitation of MOTUs are quite reasonable, new data on nuclear DNA as well as morphological variation are necessary for a final evaluation of the status of the various clades identified. I'm sure the authors agree to this, and certainly hope for their follow-up along such lines.

In reviewing the previous version, I pointed out that there was no mention of how gaps in the alignments of sequences were treated. This omission has not been corrected in the present version, but such information is required. There are often no gaps in CO1 alignments of close relatives, but this cannot be said for 16S alignments.

Some details:
L 42: Daphnia O.F. Müller, 1776 should be 1785 (Müller 1776 wrote Daphne, not Daphnia)
L. 87-88: I don’t understand how the reference to the FADA list (Kotov et al. 2013) supports this statement
L. 304: Difficult sentence. You need at least to add “and” before “39 original”
L. 367: Replace FigurebS4 with Figure S3
L. 509: The reference to Cieplinski et al (2017) is irrelevant here, as they studied rotifers, not microcrustaceans
Figure 4, lower panel: The symbol for the J clade should be a circle, not a square
Figure 5. I’m still not happy with the legend referring to coloration – see my recommendation on the previous version. The inclusion of colored symbols on the tree branches is very helpful. However, the placement of the symbols for the G and H clades cause confusion and should be simplified. I suggest placing the G symbol closer to the G clade, and the upper H symbol at the root of the H1 clade.
Supplemental figures:  I can find no legends to these in this revised version
Experimental design: No comments
Validity of the findings: No comments
Additional comments: No additional comments


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

Input:
Title: BROWN BEAR COMMUNICATION HUBS: PATTERNS AND CORRELATES OF TREE RUBBING AND PEDAL MARKING AT A LONG-TERM MARKING SITE
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1-The article could be improved by editing for proper English.
2-The study does a good job of including relevant literature for a thorough background of the topic.
3-The article structure is good.
4-The article is self-contained.

Regarding #1, overall, the article seems like it could be improved by a thorough editing by a native English speaker. For example in the abstract:
Line 29-30: I don't understand what "automatic video recording" means. Is this a video camera trap?
Line 31: "visited more frequently" should be "more frequently visited".
Line 32: "consisted in sniffing" should be "consisted of sniffing"
Line 41-42: I don't know what "These synergies consisting" means.
You can likely get this paper through the review process as is, because these are just minor grammatical errors, but your manuscript will be taken more seriously by other scientists if you address these type of issues throughout the manuscript.
Experimental design: The experimental design is interesting and solid in design, and the methods are explained well. The main drawback is that the study is limited to only one site, but this drawback is addressed thoroughly in the Discussion.
Validity of the findings: 1-PeerJ does not assess the novelty of studies.
2- The study is limited to one marking site.
There is also a lot of interpretation used to sex and age the bears (i.e., head and neck shape), and this lack of rigour should be mentioned in the Discussion.
In addition, at times there is no distinction made between bear species, which I think could be a week part of the manuscript. For example, brown and black bears may have different behaviors based on their ecological niches.
3- Discussion and conclusions are well-written and accurate.
4- Speculation is limited.
Additional comments: This is an interesting and well-done experiment. As noted above, I encourage you to have a native English speaker proofread the manuscript to catch small grammatical errors.


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: BROWN BEAR COMMUNICATION HUBS: PATTERNS AND CORRELATES OF TREE RUBBING AND PEDAL MARKING AT A LONG-TERM MARKING SITE
Review round: 1
Reviewer: 2

Output:
Basic reporting: 1)	The paper needs a hypothesis
5)	The English needs to be edited in this manuscript
Experimental design: 2)	The analysis essentially only has one degree of freedom. A single tree is used. Because of this, the paper may be better suited for a natural history, or research note type of publication.
Validity of the findings: 3)	Visually identifying individual identity, sex, and age, needs to be validated, or the authors need to provide references where others have done this successfully for bears and have validated it. Without this, I am not confident that visually identifying individual identity, sex, and age of bears is a robust approach. Pictures showing how and why animals were identified as such would help, as would exploring the sensitivity of results to this uncertainty.
4)	Many studies of brown bears in North America detect similar numbers of females (identified via DNA genotyping) and males at rub trees (Kendall et al. 2009; Morehouse & Boyce 2016; Lamb et al. 2018). It should be acknowledged, that the results found here (9% of females rub) are either not consistent with North America, or are an artefact of only sampling a single tree.
Additional comments: This manuscript provides an interesting account of the function of pedal marking and chemical communication by brown bears at a single oak tree in Spain. The following items require attention before this work is ready for publication
1)	The paper needs a hypothesis
2)	The analysis essentially only has one degree of freedom. A single tree is used. Because of this, the paper may be better suited for a natural history, or research note type of publication.
3)	Visually identifying individual identity, sex, and age, needs to be validated, or the authors need to provide references where others have done this successfully for bears and have validated it. Without this, I am not confident that visually identifying individual identity, sex, and age of bears is a robust approach. Pictures showing how and why animals were identified as such would help, as would exploring the sensitivity of results to this uncertainty.
4)	Many studies of brown bears in North America detect similar numbers of females (identified via DNA genotyping) and males at rub trees (Kendall et al. 2009; Morehouse & Boyce 2016; Lamb et al. 2018). It should be acknowledged, that the results found here (9% of females rub) are either not consistent with North America, or are an artefact of only sampling a single tree.
5)	The English needs to be edited in this manuscript
Abstract: “consisted in sniffing” to “consisted of sniffing”
“Capitalized” to “dominated”?
“more likely if other individual” to “more likely if another individual”
“obtain important information at population level”- what kind of information? How do you know?
L51-mating  or finding and attracting mates?
L57-60- Urine doesn’t provide information on reproductive status?
L73- “in” to “to” and “at population level” to “at a population level”
L86- the other paper I know of for this is “Lamb et al. 2017, Plos One” which is cited elsewhere in the paper, but could be added here.
L96- make the hypothesis clear here. Do you expect Pedal marking to be additive to tree rubbing? Ie. Same information transferred, but just more effectively, or, does the pedal information interact with tree rubbing information and together they paint a picture?
L102- how did they communicate before 2002? Or were they few in number before then?
L114- what is the population density? In bears/1000km2
L122- choosing only a single tree is surprising, this severely limits effective sample size and inference.
L139- define zenithal in this context. Is this looking down from the tree onto the rubbing area? And when was this change made?
L149- I would like the authors to add additional information on how they visually identified individuals, sex and age-class. Specifically, an analysis of the classification accuracy and repeatability of visual identification would be insightful, especially within and between years. Other works have visually identified bears, notably Larry Aumiller, who ran McNeil Falls for 25 years could supposedly do this.  But he watched the bears every day from a close range.  A lot was by how they walked, how they fished, who they got along with.  He knew the bears all very well. I do not think that individual identity, sex, and age of bears can be reliably determined from camera trap footage of bears (even though others have done this, but with no validation as to whether the classification was correct [Clapham et al. 2012]). I would like to see numbers regarding the accuracy of these methods. Especially because large classification error rates could significantly change the results of the current manuscript.
L265- is it possible that animals are still receiving signals even when you don’t see them sniffing? Maybe they only need to sniff when the signal is weak- after time has elapsed.
L328- discuss the sex and age classes most likely to receive these signals. What are they supposedly interpreting from these signals? Do these patterns change through the seasons?

References:
Kendall, K.C., Stetz, J.B., Boulanger, J., Macleod, A.C., Paetkau, D. & White, G.C. (2009). Demography and Genetic Structure of a Recovering Grizzly Bear Population. J. Wildl. Manage., 73, 3–17.
Lamb, C.T., Mowat, G., Reid, A., Smit, L., Proctor, M.F., McLellan, B.N., et al. (2018). Effects of habitat quality and access management on the density of a recovering grizzly bear population. J. Appl. Ecol.
Morehouse, A.T. & Boyce, M.S. (2016). Grizzly bears without borders: Spatially explicit capture recapture in southwestern Alberta. J. Wildl. Manage., 80, 1152–1166.


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: BROWN BEAR COMMUNICATION HUBS: PATTERNS AND CORRELATES OF TREE RUBBING AND PEDAL MARKING AT A LONG-TERM MARKING SITE
Review round: 2
Reviewer: 1

Output:
Basic reporting: Generally good English throughout, but could be improved.

Terminology could also be improved (referring to 'bears' and assuming the reader knows that it is brown bears rather than bears of the family Ursus)
Experimental design: Acceptable.
Descriptive in nature.
Could be improved with simple descriptive statistics, rather than just providing proportions/means.
Validity of the findings: Acceptable
Additional comments: Brown bear communication hubs: patterns and correlates of tree rubbing and pedal marking at a long-term marking site (#32708)

My main comment is that the analyses should become more rigorous, rather than purely descriptive.
-Analyses (Lines 200-213) and Table 1. Why are the age and sex of individuals not considered for each behavior? Even if some behaviors are performed by just males or adults, this would be important to analyze. Please use the age and sex variables for each behavior.
-Lines 221-222: Rather than saying that others species are “considerably” less frequent. Please analyze statistically and tell us if bears are significantly more frequent. (Make this explicit statistically rather than purely descriptive and lacking rigor).
-Lines 225-227: It would be helpful to plot the time of use in the overlap package and provide a figure.
-Lines 227-228: Again, rather than just saying they are more frequent visitors during breeding season, please analyze this statistically.
-Lines 243-284: rather than just reporting percentages of behaviors by each age and sex class, it would be helpful to actually analyze these to see if they are significantly different. This could be easily done with chi-square tests.

Other comments include:
-I would suggest using the term “camera trap” throughout the manuscript, rather than “camera”, “automatic camera” or other terms.
-You have made many clarifications to your responses to us (editors/reviewers), but these clarifications often have not made them into the manuscript.
-Your use of ‘bears’ to denote brown bears throughout the text is confusing. I think you should specifically mention the bear species at each instance of ‘bear’ rather than having the reader make assumptions about if you are talking about the family Ursus or a given species.
-Line 71. Please define “synergy”. I tend to view communication as a competitive behavior rather than a cooperative behavior. For example, two territorial male bears will leave scent to show their dominance and enhance their odds of being chosen to mate with by a female. I don’t think this is a cooperative behavior between the two males.
-Lines 102-106: Please justify why you used just one marking site. Is this site unique in some way? Or is it typical? You need to justify this for future readers of the article.


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: BROWN BEAR COMMUNICATION HUBS: PATTERNS AND CORRELATES OF TREE RUBBING AND PEDAL MARKING AT A LONG-TERM MARKING SITE
Review round: 2
Reviewer: 2

Output:
Basic reporting: The paper still feels "over-sold" to me. There are many hyperbolic statements suggesting this is a "long-term" study, or that the results could inform what brown bears do generally. I do not feel that is the case at all. Monitoring a single tree for 4 years is neither long term nor broadly applicable.
Experimental design: The statistics need additional attention and analyses
Validity of the findings: I still feel this work needs much more qualifying of the results, due to the small sample, and unique situation of a single tree used by a recovering, low-density bear population.

I would also like to see the authors have a few independent persons try to identify individual bears based on their criteria. And calculate the repeatability and accuracy of this approach.
Additional comments: Title and L29: Long-term generally refers to studies of > 20 years. 5 years of data collection for a mammal that can live for >30 years would not be considered long term. All references to long term should be removed. Even if the long-term is referring to the long-term duration of this one tree by bears, that time is unknown (aside from atleast 2002-2016) so, also warrants removal or clarification as well.

L28, who is “their” referring to? The chemicals? The bears?

L99: I should have phrased comment about the hypothesis from the last round differently. Yes, the authors alluded to having a hypothesis, but it was vague, and arguably not falsifiable/testable.  “hypothesize that pedal-marking and tree-rubbing are deeply linked, forming a more complex communication system than previously recognized” is a subjective, unfalsifiable claim as far as I am concerned. I would like to see a specific, mechanistic hypothesis. “we hypothesize that tree-rubbing are deeply linked because….we expect to find adult male biased marking behavior during X season because…” Then list your testable predictions.
“
L111: remove any plural, such as “these communication hubs” given that the authors only have a single tree. N=1.
L210: shouldn’t individual be a random effect to, due to the repeated observations

L228: Table 3 needs to be converted to standardized coefficients, and these need to be model-averaged, given that there are many competing models for each analysis.

L228 (table A7 Results of the models within ΔAIC < 2 of the best model): how do the authors justify their paper being largely about age and sex effects, when age and sex effects are only in 1 of the top AIC models for each of the 5 analyses.
L241: the 22% and 87% # below don’t make sense to me. In 22% of visits there was no communication behavior, but in 87% of visits there was chemical communication?
L263:296: I think there needs to be some statistical tests associated with all of these %’s reported. Are these comparisons statistically different? Ie., I suspect “Males sniffed the tree in 59% of their visits, while adult females did so in 51% of their visits” would be statistically indistinguishable.
L327: describing “January 2012 and January 2016” as a “very long time period” is a major stretch. I suggest just saying 4 years. Especially given that not all data during that period were even used

L337: suggest adding “ for brown bears living at low densities in Spain”. I don’t expect all of these results to be generally applicable across the brown bear range. Partly because I suspect the n=1 nature of this study will be sensitive and extrapolate poorly, but also that brown bears have different behaviours, life histories and stressors across their range that will influence even a solid inference.


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: BROWN BEAR COMMUNICATION HUBS: PATTERNS AND CORRELATES OF TREE RUBBING AND PEDAL MARKING AT A LONG-TERM MARKING SITE
Review round: 2
Reviewer: 3

Output:
Basic reporting: This review was requested as an additional, partial review to address statistical concerns, in particular several raised by the Academic editor.

Minor comment

It would be nice to see some of the main conclusions in the abstract.
Experimental design: Which package and version in R was used to calculate the GLMMs? Was it lme4? This should be stated and cited.
Validity of the findings: 1. Problems with pseudoreplication
The data is definitely pseudoreplicated. As individuals are known to have made multiple visits, the sample size is inflated. I don’t think this is necessarily an insurmountable problem, but it needs to be addressed more than it has.

Either a really careful interpretation of the results needs to be made, or a solution (partial solution) needs to be attempted. One potential solution (not perfect but better than nothing) would be to add ID as a random factor [a crossed, not nested random factor, i.e. with lmer this would be (1|year) + (1|id)]. Identify the bears which can be identified, and identify all other visits as “unknown”. This would result in lumping all unknown visits together, erring on the side of being overly conservative (opposite to the current situation). Both options (not conservative enough, vs. overly-conservative) have their draw backs.

2. Age-sex class for visits
Why isn’t age-sex class included as a parameter in the model looking at the probability of a bear visit? One of the main, and potentially most straightforward conclusions is that adult males make more visits than any other class. It would be great to have this backed up by statistics.

3. Analysis and Information Theoretic approach

a) Model Assumptions and Valid Model
The first step in Information Theoretic approach is to make sure that the full (or global) model satisfies assumptions and is a good fit to the data.

In this case, I would suggest that the authors check for multicollinearity (ie. use a metric like VIF to identify problematically correlated variables). For example, time since last male visit and time since last visit with pedal marking might be problematically correlated.

Also check for overdispersion, and address it if necessary. With many zero visit days, overdispersion is a risk and makes the results look more 'significant' than they really are. Ben Bolker has a good reference for testing for, and addressing overdisperion in lmer (https://bbolker.github.io/mixedmodels-misc/glmmFAQ.html#overdispersion)

The full models should also be checked to make sure they fit the data reasonably well i.e., calculate the marginal and condition R2. Nakagawa and Schielzeth (2013) present a good way of doing so for mixed models and the MuMIn package includes a function based on their method: r.squaredGLMM().

Nakagawa S, Schielzeth H. 2013. A general and simple method for obtaining R2 from generalized linear mixed-effects models. Methods in Ecology and Evolution. 4(2):133–142.

b) P-Values
Information Theoretic (IT) approach is an approach for model selection. So technically if AIC is used to select a model, the traditional results of that model (including P-values) can be presented. However, most researchers using AIC do not present p-values because of the philosophical differences between IT and Hypothesis testing. In the IT framework, it is better to present confidence intervals (CI) around the effect. Since, mathematically CIs work out pretty much the same as P-values, cause less friction (philosophically), AND are generally considered superior to P-values (even in hypothesis testing), I suggest presenting the results as the effect with 95% Confidence Limits (see below for how to do this with MuMIn).

c) IT Model selection and interpretation
Using IT in this study is makes perfect sense, given the type of questions being asked. However, I feel that the process isn’t quite finished. The main problem is that, with one exception, every analysis ends up with multiple models, and it is unclear why only the ‘best’ of these multiple models is presented in Table 3 (one of the main benefits of IT is that is recognizes that there may be several models with similar support). If only these models are considered, the analysis looses a lot of information.

Using IT like this, to choose just the best model does happen, but not advisable (because of situations like this, where many of the top models are pretty close to each other).

I would recommend model averaging. The MuMIn package in R has a built in function for this: model.avg(). Instead of using a cutoff of 2 delta AIC, I would use the 95% confidence set (which will often include more models, but has better theoretical support than an arbitrary cutoff). It is straightforward to also calculate the confidence limits around the averaged parameters. There are specific examples in the documentation of MuMIn’s model.avg() function for how to achieve this in R (ie. ?model.avg).

This reference provides details on model averaging and on using the 95% confidence set:

Symonds MRE, Moussalli A. 2011. A brief guide to model selection, multimodel inference and model averaging in behavioural ecology using Akaike’s information criterion. Behavioral Ecology and Sociobiology. 65(1):13–21.

An overall article that addresses many of these issues (https://peerj.com/articles/4794/)

Harrison XA, Donaldson L, Correa-Cano ME, Evans J, Fisher DN, Goodwin CED, Robinson BS, Hodgson DJ, Inger R. 2018. A brief introduction to mixed effects modelling and multi-model inference in ecology. PeerJ. 6:e4794. doi:10.7717/peerj.4794.

d) Presentation of the results
Right now these results are a bit confusing because the results overlap between Table 3 and Table S7 and could be clarified.

I would recommend making Table 3 the results of model averaging including effects +/- confidence intervals, full model R2, etc. Include all parameters in the confidence set of models, whether or not the CI 95% includes 0. This makes it easy for readers to quickly scan the results and see which parameters are interpretable and which are not. Also be sure to clarify what each parameter means in the table (i.e. what does a positive effect of season mean?). Note that here, the effect of age_sex is always compared to females, i.e. each estimate shows the difference between an age-sex class and the females. As males seem to be the most different, perhaps they should be used as the contrast (or consider a post-hoc test to tease apart the differences).

In each analysis, there are not too many models in the candidate set. Therefore, I would suggest including all models for each analysis in the Table S7, ranked by AICc (as they currently are), and using cell shading or some other type of formatting to indicate of which models were in the confidence set (i.e. which included in model averaging) and which were not. I would remove all parameter estimates from Table S7, and simply indicate whether or not a parameter was included in the model or not.

An example of the presentation of results, both model averaged results (Tables 2 and 3) and model selection (Appendix tables). Note that Tables 2 and 3 present the results of three different models each (one in each column). This is just an example, there are other ways of presenting the results.

LaZerte SE, Otter KA, Slabbekoorn H. 2015. Relative effects of ambient noise and habitat openness on signal transfer for chickadee vocalizations in rural and urban green-spaces. Bioacoustics. 24(3):233–252. doi:10.1080/09524622.2015.1060531.
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: BROWN BEAR COMMUNICATION HUBS: PATTERNS AND CORRELATES OF TREE RUBBING AND PEDAL MARKING AT A LONG-TERM MARKING SITE
Review round: 3
Reviewer: 1

Output:
Basic reporting: The grammar could be better, and some of the terminology is confusing. For example, the authors say 'brown bears (hereafter bears)', but then continue to switch between 'brown bears' and 'bears' for the rest of the paper.

Previous reviewers previously made suggestions on how to improve the readability of the manuscript, but the authors rebutted most of the suggestions. The comments were not personal attacks on the authors, but were apparently taken as so, leading the authors to take a combative stance. Even if you do not like the proposed changes, they point to areas of the manuscript that need improvement. Just rebutting suggestions based on "personal preference" doesn't fix the problem.

The authors are clearly uninterested in further peer review of the manuscript, but I don't believe it is ready for publication. I would encourage more mature responses in the future.
Experimental design: Descriptive.
See past reviews. Authors do not seem interested in considering other methods of analyses. They also refer to past versions of the manuscript, which readers will not have access to, when rebutting changes.
Validity of the findings: Valid.
Limited by being just one site.
Limited by analyses used (and authors are unwilling to consider others).
Additional comments: I would encourage the authors to make more of a good faith effort to address reviewer comments in the future. I can understand the authors may be frustrated, but being rude to reviewers doesn't do anyone any good. This was possibly the worst response to reviewer comments I have ever seen.


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: BROWN BEAR COMMUNICATION HUBS: PATTERNS AND CORRELATES OF TREE RUBBING AND PEDAL MARKING AT A LONG-TERM MARKING SITE
Review round: 3
Reviewer: 2

Output:
Basic reporting: Including conclusions in the abstract

The authors do include detailed results in the abstract, and broad conclusions, but not what I would consider a study-level conclusion. For example, in the discussion on L310-312, a clear conclusion is made: “Our results, in accordance with published information, show that tree rubbing can be performed by any class of individual at any time, but it is clearly monopolized by adult males, especially during the mating season”. I would suggest that adding this kind of statement to the abstract makes the abstract much more interesting and informative. However, I feel a bit like I’m quibbling over the details, so I leave it up to the authors to decide whether or not they want to make any changes.

L223. Consider adding a small note explaining that pedal marking models only included males because it was performed almost exclusively by males. I realize this information is in the results, in Table 1, AND in Table 3, but there are many models and a lot of information which can make it easy for a reader to miss important details. As this is the only model that deals just with males, adding something here might help guide the reader along.
Experimental design: Alpha
In the results, authors consider all effects where the P < 0.10. This is completely fine, but most readers would assume an alpha of 5%. Therefore, I suggest noting in the methods that an alpha of 10% was used to evaluate the results.

L218 R packages should get their own citations both in text and in the references. This ensures the authors of open source software get credit for their work. Including the package version makes the research more reproducible. You can use the R funciton citation(“gml”) to get the recommended citation for any package, as well as the function packageVersion(“gml”) to quickly get the version of the package.

For example (using citation info for lme4 and MuMIn, and the versions on my computer):

Analyses were performed in R v3.3.3 with packages gml(vX.X.X REF), lme4 (v1.1.21 Bates et al. 2015), and MuMIn (v1.43.6 Bartoń 2019).

Kamil Bartoń (2019). MuMIn: Multi-Model Inference. https://CRAN.R-project.org/package=MuMIn

Douglas Bates, Martin Maechler, Ben Bolker, Steve Walker (2015). Fitting Linear Mixed-Effects Models Using lme4. Journal of Statistical Software, 67(1), 1-48. doi:10.18637/jss.v067.i01.
Validity of the findings: 1. Pseudoreplication
I like this compromised approach. When we don’t know the unknown individuals, there is the worry that it is mostly one unknown individual. In that case, controlling for it in the model would be the correct approach. If, on the other hand, the unknowns are a large mix of different individuals (as the authors suggest), it won’t matter (as the authors found). Any readers who wonder can take a look at the supplemental material.

2. P-values
I’m fine with p-values if the authors feel strongly about them. There is definitely something to be said for including them as a familiar statistic.

3. Model Selection
The authors present compelling references for not doing model selection, especially with this dataset (observational with the potential for some correlated variables, even if multicollinearity is addressed).

I am satisfied with this rational, and have only the suggestion that they add a sentence describing how they select which models to interpret, something like:
L216/217 “From the resulting models, we report only those within ΔAIC<2, and we interpret only the best model (that with the lowest AIC)”
OR
 “From the resulting models, we report and interpret only those within ΔAIC<2”.
Which ever best describes their approach.

4. Presentation of the results.
I’m glad the authors included R2 and am fine if the authors feel like they would prefer to keep the current formatting.

However, I still feel that it should be clear in Table 3 that in tree rubbing, the effects of age_sex are all compared to the base group, females. For example, in the text (L282-284), it states that “Adult males and juveniles had higher probabilities of tree-rubbing during their visits than the rest of the individuals”.

This isn’t correct: adult males and juveniles both perform more tree rubbing than females, but indeterminate individuals were not significantly different from females. While the estimates do suggest a significant difference between indeterminate and males/juveniles, there is no statistical test confirming these differences (a post hoc test would be needed).

I would suggest changing the statement on L282-284 to something like “Adult males and juveniles had higher probabilities of tree-rubbing during their visits than females.” And would also suggest altering the text in Table 3 to something like: “Undetermined vs. Females”, “Juvenile vs. Females”, and “Males vs. Females”. Something at least to explain to the reader why females don’t appear in the Table 3.

Minor Comment:

L358-368. The “sniff tree” model only has an R2 of 0.06, which is low even for ecological/behavioural studies. Consider adding a note to that effect.
Additional comments: Overall I am satisfied with the authors responses to my comments. I have a few outstanding issues/suggestions which I have highlighted, but I do not think they are extremely problematic. I note again, that I have mostly focused on methods, and particularly on the statistics.


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

Input:
Title: DYNAMICS OF LOCOMOTION IN THE SEED HARVESTING ANT MESSOR BARBARUS: EFFECT OF INDIVIDUAL BODY MASS AND TRANSPORTED LOAD MASS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is well structured, clearly written and uses a well comprehendable language. The literature references both in the introduction and discussion comprehensively cover the field. The manuscript is very well structured and follows a clear logic. The raw data is present and in an impeccable state. The overall topic is self-contained and follows a clear question throughout.
Experimental design: The expriment is original and fits within the scop of the journal. The research question is well defined and relevant within the field of animal locomotion. It fills a knowledge gab.
The invesitation is appropriate and of high standard. The methods used are sufficiently described.
Validity of the findings: The findings are novel and hence add important knowledge to the field.
The data are provided and to my judgment the analsys is sound. The conclusions follow the data and are not over-interpreting.
Additional comments: This is a very well written manuscript, however with a one or the other typo, i.e. line 152 United Sates. Please check prior to publishing.


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: DYNAMICS OF LOCOMOTION IN THE SEED HARVESTING ANT MESSOR BARBARUS: EFFECT OF INDIVIDUAL BODY MASS AND TRANSPORTED LOAD MASS
Review round: 1
Reviewer: 2

Output:
Basic reporting: I noticed some typos and grammar errors.

The figure panels are explained in the figure legends, but adding color legends and titles (e.g. no load, small load, high load in figures 3 and 4) directly to all figures would greatly improve readability.
Experimental design: The research question was not clear to me. In lines 98-103, the authors identify the knowledge gap. But what is the specific hypothesis being tested? What is the expected effect of body mass and added load? Would differently sized/loaded animals be expected to have a different movement strategy or vary with respect to efficiency? A clear hypothesis would help streamline the manuscript (much like in Merienne et al. 2020).

The Methods section lacks some details.

Were the data in this manuscript collected as part of Merienne et al. (2020)? If so, this should be noted in the Methods section.

Please add information about the weight of the added load in the manuscript (line 151). Based on the datasheet, it looks like the load varied from ant to ant. Why was that?
Did the loads significantly affect the overall COM for each ant? By how much?

How many strides per animal were analyzed (lines 182-184)?

How are sinusoids fitted to Ek and Ep in the high-load condition, in which oscillations do not look sinusoidal (line 228 and Figure 4E,F)?

What was the rationale for expressing variables as a power law function of ant mass (lines 223-234)?

At the end of the Methods section, it would be helpful to add information on how the CIs were calculated and how they were used to determine the statistical significance of the model coefficients.
Validity of the findings: As stated above, it would help to have a clearly defined research question/hypothesis to which the conclusions can be linked to.
Additional comments: This manuscript is an interesting extension to the authors’ prior study on load carrying in ants and its effects on locomotion. I have no serious concerns about the conclusions drawn, but I have a number of additional comments (in order of appearance) that I feel should be addressed to improve the readability of the manuscript and the repeatability of the experiments.

The introduction feels very gait-centered. Based on the first paragraphs, I would have expected to see a more thorough gait analysis including leg kinematics. It would be helpful if the introduction reflected the focus of the manuscript (load-dependent movements of the COM rather than gaits) more clearly. For example, instead of introducing the concept of gaits and COM dynamics in line 46, the authors could first emphasize that insects show remarkable locomotor flexibility dependent on task/context, but that the effect of load, specifically the mechanical energy transfer, is not well understood. Then, they could introduce Messor barbarous as a model system, measuring the COM dynamics as a way of quantifying the effects of load carriage, and the specific research question(s).

How fast were the ants walking in the present study? Do the COM dynamics (amplitudes, phase shifts, …) depend on walking speed?

Line 265: “…Ek and Ep were more in phase for big ants than small ants”. Isn’t it the other way around according to Figure 5A and Table 1?

Figure 1: Why are there four/five tracked points in A,C but six points in B,D? Were the points tracked in all five camera views? Also, it would help to indicate the (overall) COM position and highlight the added load (maybe with an arrow?).

Figure 2: I don’t count 52 data points. Are data missing or were data excluded? Also, why was the distinction between small and big ants made at 10.2 mg? Is this the median weight?

Figure 5: The Welch-test was used to test small ants vs big ants. Was it also used to test unloaded ants vs loaded ants? This is what the letters “a” and “b” suggest to me (e.g., in panel A, small unloaded and small loaded ants do not differ signficitanly; they both belong to group “a”). If so, a paired test should be used instead. If not, it might be clearer to draw a bar above the experimental groups that were compared with each other rather than using letters.

Figure 6: Why is the mechanical work the only parameter that is not shown for the loaded ants?


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 COCONUT WATER ON BLOOD SUGAR AND RETINA OF RATS WITH DIABETES
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article would benefit from an English language editor who should review the entire article to improve flow, grammar and ambiguous language.

Line 39- Unsure of how non-communicable disease relates to this article. Simply put Diabetes is one of the most significant public health problems worldwide.

Line 40-Authors could substitute epidemiological data from global data of incidence of DR and PDR as rat model not specific to DM in Chinese patients

Line 44- DR is one of the microvascular complications of DM and the major ocular complication.

Line 47-The authors may want to note DR is the most common cause of vision loss in the working population

Line 50-The statement that the pathogenesis of DR is unclear is misleading. The authors should expand on the role of hyperglycaemia, pericyte death and inflammatory cytokines such as VEGF while noting limitations. Additionally there are specific limitations of animal models which may further put this article into context. (Kern T, S, Antonetti D, A, Smith L, E, H: Pathophysiology of Diabetic Retinopathy: Contribution and Limitations of Laboratory Research. Ophthalmic Res 2019;62:196-202. doi: 10.1159/000500026)

Line 51-The authors should note the role of anti-VEGF therapy (Protocol S) as well as, steroids, PRP and focal laser. The role of surgery is for the complications of proliferative diabetic retinopathy such as vitreous hemorrhage and tractional retinal detachment. The authors may want to expand on glycemic control and blood pressure control in prevention.

Line 52 “Early effective drug treatment is still in the exploratory stage, and so it is very important to find an effective drug treatment to prevent in the early stage of onset”…This statement is misleading.

Lines 55-63…The authors should simplify this part of introduction to state CW is abundant….some promise in regulating blood sugar, carbohydrates and reducing microvascular complications of neprhopathy…The authors wondered if there would be a role in reducing DR, another microvascular complication.

Line 64-The whole body condition is ambiguous…the authors should study what was measured and why.

Line 69- Add units to rat weight in manuscript and excel data file. Change refractive stroma to corneal stroma

Line 117- Could rephrase to “Based on an adult body weight of 60 kg, a typical initial dosage of glibenclamide would be 5 mg per day”

Line 138- The total retinal thickness was defined as the the distance between the ILM and RPE. These are relatively hyper reflective…but this statement is unnecessarily complicated.

Line 144- Could be rephrased for clarity “Diabetes mellitus in rats led to the formation of cataract which affects the signal strength of the OCT. When half the rats in a particular group were unable to have a sufficient signal strength to perform OCT, examinations in all groups were terminated to allow for comparison between groups.”

Line 193-195- The wording of these lines are clumsy. “the fasting blood sugar of group I-NC was always at normal  level (4-6 mmol/L), while the other three groups had significantly higher levels than group I (P>0.05)”

Line 206-210- These sentences could be misleading, please indicate that although there was no significant difference there was a trend for bodyweight.

Line 216-19-These sentances are confusing “Only results at week 8 and 12 were obtained as at week 16 over half of group II-DM rats had a lens opacity precluded adequate signal strength of the OCT”

Lines 221-223. Language is confusing, could be rephrased as “OCT allows for the assessment of individual layers of the retina”

Line 283- The pathophysiology of DR is complex but I would avoid describing it as very complicated.
Experimental design: Line 69- make the age of the rats less ambiguous “about 10 weeks”
The temperature range is not ideal many labs would store at 22+/- 2 Celsius. Hypo and hyperthermia may affect the glycemic control and caloric requirements of the rats.

Line 83- Using local coconuts may be convenient but may make it challenging to reproduce the results as the concentrations of sugar, vitamins, minerals, amino acids and other factors may differ between crops. An analysis of the nutrition of water fed to rats may have been helpful.

Although OCT was unable to be performed due to cataract formation beyond week 16, it would be interesting to determine the effect of coconut water in diet on the formation of visual significant cataract.

Line 167- Why did the authors choose 4 fields of view for this analysis? Additionally how were the fields chosen? Were they chosen at random and averaged? Although there is no standard others have sampled 10 areas at random and averaged. More sampled areas would likely give more reproducible results.
(Jun PENG, Kun PAN, Zheng-Rong LIU, Yu-Hui QIN, Qing-Hua PENG,
Effects of Shuang Dan Ming Mu Capsule on Expression of VEGF-a, VEGF-b, VEGF-c and the VEGF receptor, Flk-1, in Diabetic Retinopathy Rats,
Digital Chinese Medicine, Volume 1, Issue 3, 2018,Pages 228-238,)
Validity of the findings: Line 267-Retinal thickness is not an accurate surrogate for diabetic retinopathy. It is an early change in DR, however you may expect to see early microvascular changes in DR. It would have been useful if the authors by examining the microvascular changes in the contralateral eyes looking for pericyte density and considered a trypsin digest. Their rats were sacrificed at 20 weeks and likely would have demonstrated some microvascular changes. This would have strengthened their findings and allowed for a comment on DR. The authors may be limited as the experiments have already been completed and should discuss limitations related to their limited OCT, histologic and immunohistologic analysis.

Line 269-Coconut water is a natural product, unless the authors plan to assess specific molecules within coconut water they should avoid discussing coconut water as a candidate drug. Instead they should discuss its role as a nutritional supplement.

The authors assessed VEGF expression in the rat retina, however assessment of specific isoforms as well as other cytokines known to be associated with DR would have added depth to their experiments.

The conclusions are misleading and should focus on what this study demonstrated….fasting blood sugar, retinal thickness as measured by OCT and retinal VEGF expression at 20 weeks weeks were all lower in diabetic rats who consumed coconut water. We speculated this may be due to its antioxidant properties. Further studies are needed to investigate the role of coconut water supplementation in DM and which antioxidants in coconut water may be developed into candidate drugs.
Additional comments: My understanding is that the diabetic model was induced at 10 weeks age and then rats were sacrificed at week 20 of the experiment. It may be useful in the figures and text to clarify week of experiment vs week of age.

Figure 3- Although Inner and outer nuclear layers can also be referred to as granular layers, it may be best to refer as inner and outer nuclear layers as these are the preferred terminology for OCT interpretation. The resolution of the OCT scan is not ideal in this image, if possible use an image with a higher DPI and more clarity to allow for definition of the retinal layers. Additionally the rat retina should demonstrate NFL, GCL, IPL, INL, OPL, ONL, ELM, IS/OS, RPE and choroid. It may be better to use this terminology or at least label the OCT and pathology slide separately.

The authors discussion of DR and VEGF is oversimplified and they should briefly discuss the clinical pathophysiology (hyperglycaemia and pericyte death) before discussing the molecular pathophysiology where they discuss PKC, AGEs and ROS. However they do not mention the hexosamine pathway, polyol pathway, poly (ADP-ribose) polymerase activation, renin-angiotensin aldosterone system and inflammation. For a review they authors my look at (Michael Whitehead, Sanjeewa Wickremasinghe, Andrew Osborne, Peter Van Wijngaarden & Keith R. Martin (2018) Diabetic retinopathy: a complex pathophysiology requiring novel therapeutic strategies, Expert Opinion on Biological Therapy, 18:12, 1257-1270, DOI: 10.1080/14712598.2018.1545836)


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 COCONUT WATER ON BLOOD SUGAR AND RETINA OF RATS WITH DIABETES
Review round: 1
Reviewer: 2

Output:
Basic reporting: The English needs major revision throughout the paper. Multiple grammar, syntax, and punctuation errors.
The introduction is sufficient, however, some references are missing
Conforms to PeerJ article structure; however, it requires significant revision with regards to the language.
Only blood glucose and weight data are shared - OCT and histology data are not made available

Introduction:
1-	Line 46: Reference needed for the incidence of DR in Chinese DM patients.
2-	Line 50: Authors claim that DR pathophysiology is still unclear; The authors should state that it has been previously studied and is multifactorial (possibly include a short summary with relevant references)
3-	Line 50: Clarification needed for the treatment options discussed. What types of laser/surgery, accompanied by relevant references.
4-	Line 51: Reference needed for the claimed “poor prognosis”.

Figures 1-2: Statistical significance should be shown by a notation. It should be clarified what error bars represent (SD, SE, CI,..). The abbreviations in figure legends should be explained in the caption.
Figures 4-5: Areas of interest should be highlighted with an arrow (similar to Fig 6)
Figure 7 is likely not necessary, as this is not a review paper.

Table 1 - The abbreviations in figure legends should be explained in the caption; values at baseline and week 4 should be included and statistically compared (to be included in the results section as well)
Experimental design: The article fits the scope of the journal.

Methods:

- Sample size analysis to be included in the methods section.
- Although a sample size of 48 is powered (at alpha 0.05, B 0.20, small effect size 0.5) for the majority of the analyses performed by the authors, their OCT analysis is underpowered as obtaining quality OCT images was not possible in more than half of group II at 12W. The potential loss of sample through the experiment should have been accounted for in the power analysis and authors should have started with a large sample. At this point, this limitation should be mentioned in the discussion.
- The authors decided to stop OCT measurements once images were not obtainable in half of the rats in one group. This occurred at 12W in group II. However, authors could have continued obtaining OCT images in groups I, III, IIII at subsequent time points.

Line 69: The sentence should be rephrased.
Line 69: Change to Sprague-Dawley (SD)
Line 69: the units for the weight is missing
Line 103: Rats with glucose <16.7 were excluded (is it made clear in results how many? )
Line 113: Authors describe Group III as “normal rats” which contradicts their previous description of group III (diabetic rats). Such inconsistencies appear throughout the manuscript.
Line 117: “the adult body weight was 60 kg”. Unclear what authors are referring to.
Line 119: Conversion formula should be included and referenced.
Line 151: Laser treatment? – to be explained
Line 169: “Four specimens were taken from each specimen”. To be revised
Validity of the findings: Described statistical methods are sound, however, the reported results are mainly descriptive and p-values are missing at many places. More details below:

Results:
- All means and standard deviations should be included in the text.
- Precise p-values should be disclosed.
- It is unclear how many mice underwent OCT at weeks 8 and 12, at each group. Authors state that more than half of group II could not undergo OCT at Week 12; however, it should be further clarified specific to each group and each time point
- The authors should state the baseline total retinal thickness and compare across groups.
- In addition to increased retinal thickness, authors should state if any developed cystoid edema.
- Authors should report whether there were any significant differences in the fasting blood sugar level of each group prior to the commencement of the experiment/induction of DM
- Also, what is shown as week 0 in Fig 1 and 2, can be misinterpreted as pre-DM induction. I suggest that authors add the pre-DM induction values for all variables of interest to the results (and compare across the groups) and add them to the figures (as baseline). Subsequently, rename what is currently labeled as “0w” to 72h post DM induction (if that is truly what 0w is indicating).

Line 184: If 34 rates were included, success shall be 34/36= 94.4%.
Line 194: authors simply state that the fasting blood sugar was significantly higher in DM groups compared to the control. However, they state the p-value as P>0.05. Additionally, the average values shall be stated.
Line 196: Authors state that from week 4, the blood sugar increased in group II, however, in the absence of baseline values, it is difficult to apprehend the degree of increase. Further, no statistics are presented here. The same comment applies to lines 219 to 222.
Line 202: same comment as above; “P>0.05”.
Line 208: The authors report increases or decreases in weight in each group. It should be clarified to what extent these changes were, and whether they were significant.
Line 211: “glibenclamide was initiated until week 20”. It seems like week 4 is left out of the sentence. To be revised.
Line 226: Total retinal thickness values should be included in the text
Line 239-242: Authors should quantify the thickness rather than simply resorting to subjective descriptions.
Line 244: “slightly thinner”, “number of cells was decreased”, the author should clarify the comparison group and verify the statistical significance (with p-values)
Line 261-263: “p=0.00” does not make sense. Should revise (?p<0.001)

Discussion:
Line 281: The authors claim that the coconut water can effectively reduce blood sugar in diabetic rats and state that the mechanism is unknown. They should include a few theories/hypotheses about the possible mechanisms.
Line 328-336: Authors attempt to address possible pathways through which coconut water can decrease VEGF expression. It is also possible that lower blood sugar levels limited VEGF over-expression, to begin with.
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: EFFECTS OF COCONUT WATER ON BLOOD SUGAR AND RETINA OF RATS WITH DIABETES
Review round: 2
Reviewer: 1

Output:
Basic reporting: I recommend again that an English language editor review the entire article.  The authors track changes document identify many errors which can rapidly be revised. There are numerous new errors in spaces, tense and flow after incorporating the revisions.
Experimental design: I was very pleased with the rebuttal by the authors and feel their methods are justified.
Validity of the findings: No comment
Additional comments: I am pleased with the authors rebuttal and incorporation of revisions to the text. I think the experimental design and validity of the findings are appropriate for publication in the journal but not in its current form as the authors have many errors in punctuation, grammar, syntax, and flow that could rapidly be improved by an English language editor revising the document. This was recommended to them in the last review. I recommend they do this.


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

Input:
Title: A SYSTEMATIC REVIEW AND REALIST SYNTHESIS ON TOILET PAPER HOARDING: COVID OR NOT COVID, THAT IS THE QUESTION
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper consists of three parts: A systematic review of studies on (determinants of) hoarding during the COVID-19 pandemic ("primary outcome"), a systematic review of inadequate use and hoarding of toilet paper in relation to mental health outcomes ("secondary outcome"), and a review of four predictors of hoarding that may be enhanced during the COVID-19 pandemic ("realist review"). Unfortunately, I am not convinced that these parts form a coherent whole. Moreover, I have severe doubts that enough data on the central topic are available to justify a systematic review.
Experimental design: A central problem is that the paper conflates hoarding as a clinically relevant mental health issue with 'hoarding' in the form of increased purchases in response to COVID-19. The authors discuss the use of clinical and non-clinical samples (l. 115-116). Yet, this does not address the implicit assumption that these two kinds of hoarding are the same or related constructs. Although I am no expert on clinical psychology, I find this highly doubtful. If a connection between these two constructs is made, it has to be supported and defended much more strongly.

Second, it is not quite clear which role toilet paper and the COVID-19 pandemic play in the reviews. The first part of the systematic review considers hoarding during COVID-19 (but not necessarily toilet paper). The second part considers inappropriate use of toilet paper (but not necessarily during COVID-19). Finally, the realist review sometimes focuses on toilet paper-specific outcomes (e.g., mechanism 1), but sometimes discusses hoarding more generally (e.g., mechanism 3). Ultimately, these three parts do not really hang together. There also exists little data which would allow for integration (e.g., there is no data providing evidence as to whether hoarding of toilet paper is in any way distinct from other hoarding behaviour, in either clinical or non-clinical populations). This suggests that the focus of the paper is too broad.
Validity of the findings: The first part of the systematic review examines studies on hoarding during COVID-19. At this point, data is extremely limited; the systemic review only highlighted two empirical studies. Importantly, preprints were included from the systematic review. The authors identify one preprint with empirical data (Columbus, 2020). However, there are several other preprints that report on purchasing behaviour during the COVID-19 pandemic (e.g., Bai et al., 2020; Bentall et al., 2020; Zettler et al., 2020). Given the limited available data, I find it problematic that preprints are excluded from the review. Even including preprints and generalising beyond toilet paper, however, there is scarcely enough literature on hoarding during the COVID-19 pandemic to justify a systematic review.

In contrast to the systematic review, which focuses on published literature, the realist review covers a wide range of publications. These not just include preprints, but also news articles and blog posts. Some of these make rather silly arguments (e.g., a Freudian analysis of "regression to the anal stage", l. 506-507---although I understood at least one of the cited authors to be using this as a toy example to explain Freudian reasoning of which they are critical). At times, the realist review is mostly essayistic in nature. For example, l. 426-439 discuss information diffusion on social media using the example of a toilet roll juggling challenge. It is not clear what to draw from such discussions, especially since the paper does not provide even a limited review of the actual empirical literature on the topic.
Additional comments: Minor issues
l. 260 describes the findings of Garbe et al. (2020) as 'excessive stockpiling'. However, the actual item simply referred to having more toilet paper than usual at home. This is plausibly described as stockpiling, but not excessive.

References
Bai, M. (2020). Who Bought All the Toilet Paper? Conspiracy Theorists Are More Likely to Stockpile During the COVID-19 Pandemic. Retrieved from https://psyarxiv.com/z2g34/
Bentall, R. P., Lloyd, A., Bennett, K., McKay, R., Mason, L., Murphy, J., … Shevlin, M. (2020). Pandemic buying: Testing a psychological model of over-purchasing and panic buying using data from the United Kingdom and the Republic of Ireland during the early phase of the COVID-19 pandemic. Retrieved from https://psyarxiv.com/u7vqp/
Columbus, S. (2020). Honesty-Humility, beliefs, and prosocial behaviour: A test on stockpiling during the COVID-19 pandemic. Retrieved from https://psyarxiv.com/8e62v/
Zettler, I., Schild, C., Lilleholt, L., Kroencke, L., Utesch, T., Moshagen, M., … Geukes, K. (2020). Individual differences in accepting personal restrictions to fight the COVID-19 pandemic: Results from a Danish adult sample. https://doi.org/10.31234/osf.io/pkm2a