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: PHYLOGENOMIC ANALYSIS OF 589 METAGENOME-ASSEMBLED GENOMES ENCOMPASSING ALL MAJOR PROKARYOTIC LINEAGES FROM THE GUT OF HIGHER TERMITES
Review round: 1
Reviewer: 3

Output:
Basic reporting: Basic reporting is largely acceptable.  The methods section provides a list of methods used and the results are succinctly described.

In general, the primary deficiency in the manuscript as written is that I found the methods and figure legends to be incomplete. The methods and figure legends provide only the most basic information on what was done, without sufficient information regarding how the methods were applied to thoroughly evaluate their results.  The most concerning absence is the lack of information regarding how the various genome trees were generated, discussed below in the experimental design section.

However, a more abstract concern is that I’m not completely convinced that this is an adequate publishable unit.  I realize that PeerJ does not have a novelty or impact requirement, but in general, I found myself disappointed by the analyses presented.  The authors present a series of phylogenetic trees of MAGs, but don’t really do much analysis of any of the MAGS beyond that.  Most of the manuscript text is a series of paragraphs summarizing each tree and then writing out a few sentences reviewing what is known about each phylum’s role in the termite.   I’m guessing the authors are hoping in the future to then analyze the genomes and use them to gain information about their roles in the termite gut, but without that they’re left with a somewhat empty paper.  Even the trees are so summarized as to be largely useless except in the context of future analyses of these groups.  Essentially, this manuscript reads as a glorified genome announcement.

I’d really like to see *something* more, even if that’s just pairing their genome trees with 16S trees placing as many of their MAGs as possibly within the phylogenetic framework they laid out in DictDB, and potentially even linking them to 16S-based surveys of gut microbiome composition and providing quantitative analysis of which groups are under or over-represented in MAGs vs 16S.  This would at least build on the strength of the manuscript as presented.

Even better would be picking out a couple of pathways/metabolisms of interest and doing a BLAST search for key marker genes of each in all of their genomes.  A comprehensive analysis is likely beyond the scope, but even just a list of which groups have well-characterized marker genes for nitrogen fixation, acetogenesis and methanogenesis would help.  I realize that the genomes are incomplete, so lack of a marker is not evidence of absence, but presence of key marker genes is still evidence of the capability to carry out that metabolism and could provide new information regarding the roles of these microbes in termite gut metabolism.

Line 230-232.  This statement would appear to directly contradict the following paragraph, where you talk about impacts of host diet on taxonomic patterns.

Lines 247-254:  I’m having trouble deciphering this section.  First, I found it out of place at the end of a paragraph discussing the relative abundances of different bacterial groups across samples.  Further, I’m having trouble following exactly what they are trying to say.  “The number of assembled reads is negatively correlated with MAG relative abundance”: do they mean the fraction of total reads mapped to all MAGs, the fraction of reads mapped to MAGs that were in medium/high quality MAGs, or the average abundance of medium and high quality MAGs?  Why is this useful to know?  I can’t make heads or tails of the last two sentences, either, but this may be because I can’t figure out exactly which measures of relative abundance they are referring to in which parts of these sentences.
Experimental design: The largest problem with the experimental design is the lack of information regarding the genome alignments and genome tree construction.  The authors specify how the alignments and trees were constructed in terms of program parameters, but don’t lay out the results of those analyses, only the trees.  As the genome trees are the primary data being presented, the authors need to provide detailed information regarding their alignments, including, at a minimum, a list of the 43 genes used in their concatenated alignments, how many were present in each of the MAGS, and how the authors compensated for fact that many of the MAGS likely lacked multiple genes.  The authors state that they used an automated filtering algorithm for deciding which columns of the alignment were used; the number of alignment columns used in each analysis should be listed in the figure legends, as well as information regarding whether this filter effectively eliminated any of the conserved genes from consideration in construction of the genome trees.

Lines 179-181:  It seems odd to me that the authors report ‘relative abundance’ as fraction of mapped reads.  As the MAGs differ in length and completeness, shouldn’t a length-corrected (or completeness-corrected) abundance value be provided?  Or was this an attempt to simplify?  Regardless, the way in which abundance was calculated should be summarized in the Figure 3 legend to make the work more readable.
Validity of the findings: My primary concern is that I can’t really put a finger on what, exactly, their findings are.  Even their conclusions section reads mostly as a genome announcement, saying that they have constructed a resource that will be of use to the field as a whole.  As far as the rest go, they created a bunch of MAGS and genome trees for those MAGS, but don’t really go much further than that.  For all the corresponding author’s interest in termite gut symbiont phylogeny, they don’t even place their MAGS within the phylogenetic framework laid out in DictDB.

On the other hand, at least this publication will call attention to a potentially useful resource for other scientists, which can then be cited in future studies that make use of this data.  So I leave it up to PeerJ to determine what a minimally publishable unit is, should the authors be opposed to further revision
Additional comments: There are no obvious scientific errors in what is presented, although as specified above some experimental details are lacking.  Further, this was clearly a lot of work.  However, given the extent of their dataset, I find myself deeply disappointed that the authors chose not to take their results any further.  As is, this is a moderately useful genome announcement that can be cited in future studies using these resources.


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: PHYLOGENOMIC ANALYSIS OF 589 METAGENOME-ASSEMBLED GENOMES ENCOMPASSING ALL MAJOR PROKARYOTIC LINEAGES FROM THE GUT OF HIGHER TERMITES
Review round: 2
Reviewer: 1

Output:
Basic reporting: Good.  The language is largely clear and the article is well-written.
Experimental design: Good.  I remain disappointed that the authors do not do more with their data, but agree that this will be a good supplemental resource for future analyses of these genomes.  I appreciate the addition of the 16S analysis, and fell it enhances the manuscript.
Validity of the findings: The authors appear to have attempted to clarify lines 247-252: “Obvious patterns in the taxonomic distribution of the MAGs according to the sample origin were not apparent…” This seems to have been an attempt by the authors to clarify a sentence that was previously noted as confusing, but I think they’ve just made it even more confusing, especially as there are clear differences in the recovery of different phyla from different samples (most obviously, only Firmicutes were obtained from the midgut).  Maybe just go with “The taxonomic diversity of MAGs recovered is broadly representative of that observed in previously published 16S rRNA surveys, suggesting good taxonomic coverage of termite-associated microbes” or something along those lines?
Additional comments: I appreciate that the genomes are uploaded to the Assembly database, although if Genbank permits it would be helpful to have the annotations uploaded as well rather than simply the raw sequences.


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: IMPROVING SUSTAINABLE USE OF GENETIC RESOURCES IN BIODIVERSITY ARCHIVES
Review round: 1
Reviewer: 1

Output:
Basic reporting: Overall, this is an excellent, concise manuscript with clear objectives and a logical flow throughout. The main questions asked by the authors are of relevance to any researcher working not only with museum collections but performing DNA extractions from any tissue.

I have a few minor comments pertaining to figures, one suggestion for an added citation, and a handful of comments relating to spelling/grammar.

Lines 97-98, the authors state that “previous studies have not tested the correlation between age and extraction success…”; there is a reference that should be cited here:
Chambers & Hebert. 2016. Assessing DNA Barcodes for Species Identification in North American Reptiles and Amphibians in Natural History Collections. PLoS ONE https://doi.org/10.1371/journal.pone.0154363
While Chambers & Hebert (2016) examined tissue age vs DNA barcode sequence length rather than extraction success, I think it is still relevant to include their results in this manuscript.
In general, all the figure captions need to provide more detail. Also, I suggest removing the titles from the actual figure images. For all figures, perhaps instead of the figures mentioning the experiments only (e.g., “Total DNA yield vs tissue mass in Experiment 1”), there could be some additional descriptive text that allows the figures (paired with the captions) to stand alone, without the reader heaving read the text.

For the Figure 1 caption, when the authors state “the red line indicates the correlation…”, it would be helpful to also state the statistical method that was used to determine this correlation (Pearson’s correlation), and also relevant results (R2 value, p-value, etc.). The same applies to the methodology represented in Figs. 2 and 3.

Minor grammatical/formatting comments:
ll. 71-72, 74-75, 79, 344: References not in chronological order.
ll. 92: change “sample” to “samples”.
ll. 93: change “for use by molecular” to “for use in molecular”.
ll. 233: Missing closing parenthesis.
ll. 245: Should be “its”, not “it’s”.
ll. 367: Change “shot-gun” to “shotgun” to stay consistent with the rest of the ms.
ll. 369: Add comma following “material”.
ll. 379: Change “to end to the” to “to end the”.
ll. 387: Change “This solution however,”; awkward.
Experimental design: I appreciated that the authors maintained consistency throughout the ms through the use of four experiments; this made it easy to keep track of and also the experimental design was thoughtfully laid out and was easy to follow logically to complete goals.

A few minor comments:
Lines 127, 129: How was “complete tissue digestion” or “level of tissue digestion” quantified?
Lines 149-150: Why was elution buffer volume doubled, contrary to kit recommendations?
Lines 160-161: It would be helpful to have a citation here for the amount of DNA recommended to perform genome sequencing.
Validity of the findings: I have no comments for improvement of the discussion; it is well laid out and easy to follow. One suggestion that I think would be of interest to researchers is a short comment by the authors on the utility of RNAlater for preserving tissues in the field; this seems to be becoming more common practice among researchers, and a comment in the discussion (perhaps as a future direction of research) might be worthwhile.
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: IMPROVING SUSTAINABLE USE OF GENETIC RESOURCES IN BIODIVERSITY ARCHIVES
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment, see general comments for my review
Experimental design: No comment, see general comments for my review
Validity of the findings: No comment, see general comments for my review
Additional comments: My entire review is contained in these general comments.

This manuscript addresses the quantity and quality of DNA coming from frozen herpetological tissues. The purpose is to create some benchmarks for how much tissue is needed to get sufficient DNA in a world of finite tissue resources. This manuscript fills an interesting vacant niche in the literature, in the sense that most of the articles now appearing on this subject address DNA from historical museum specimens. Not many people are thinking much at the moment about preserving the DNA actually in frozen tissue collections (aside from tissue collection managers!). But it is an important issue worthy of highlighting, and the results are interesting and in some cases counter-intuitive, especially:

•	The larger the tissue mass, the more decreasing returns of DNA per tissue mass
•	DNA amount does not decrease with length of time in the freezer

I think the authors could do a bit more to place the topic in the broader context of museum collections and ancient DNA, and as it stands the literature cited is a bit thin, so they could definitely expand it out. For instance, if tissue runs out, why can’t we just use bits of the specimen? Well, for herps there is the issue of formalin preservation, which is addressed in recent publications:

Hykin, S.M., Bi, K. and McGuire, J.A., 2015. Fixing formalin: a method to recover genomic-scale DNA sequence data from formalin-fixed museum specimens using high-throughput sequencing. PLoS One 10: p.e0141579.

Ruane, S. and Austin, C.C., 2017. Phylogenomics using formalin‐fixed and 100+ year‐old intractable natural history specimens. Molecular Ecology Resources, 17: 1003-1008.

In terms of experimental design, the study is solid. On the one hand the experimental design is quite thorough and the authors have large sample sizes and address four separate experiments:

1.	Does eyeballing tissue size give you enough DNA for most uses?
2.	What is the best and smallest mass to get you there?
3.	How consistent is DNA yield from specific tissue sizes?
4.	Does age of the frozen tissue matter for DNA yields?

There are a few weak spots in their experimental design, but I do not think they are fatal to the study. For example, as the authors acknowledge, they use an extraction method that is not very common. But they do this in service of getting very standardized quantities that minimize human error, and there is no reason to think the results will not be generalizable to other, more common extraction methods.

Another small issue with Experiment 1 is that, because they combined two experiments within one (does the eyeball method produce enough DNA and is mass correlated with DNA), their masses ended up clumped around middle values, so a big part of the correlation is just driven by the four points on the higher end of the mass spectrum. Again, not fatal, but worthy of mentioning.

Ln 243-251 As for findings, I did not feel the results section for experiment 3 answered the question posed. Only means are reported, not consistency measures.

In the conclusions, the authors could significantly tighten up the writing as there is much redundancy within the conclusions and with other parts of the Discussion.

Overall this was a nice, solid study.

Minor comments:

ln 245 its
Ln 264 remove “while”
Ln 291 remove one of the “that”'s


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: HOMEOPROTEIN OTX1 AND OTX2 INVOLVEMENT IN RAT MYENTERIC NEURON ADAPTATION AFTER DNBS-INDUCED COLITIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: In the introduction section the nomenclature for chromosomal positions is not correct. Please Change the description for OTX1 and OTX2 into 2p15 and 14q22, respectively.

In the result section the text would gain understandability if each chapter ends with a short summary.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The paper submitted by Bistoletti and coworkers deals with the role of homeodomain proteins OTX1 and OTX2 in DNBS-induced colitis in rats. The study is well performed and written.


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: HOMEOPROTEIN OTX1 AND OTX2 INVOLVEMENT IN RAT MYENTERIC NEURON ADAPTATION AFTER DNBS-INDUCED COLITIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is well structured. The findings are interesting, however, it is missing important information related to the modulations observed and mechanisms.
- Abstract: Ok
- Introduction: The introduction could be improved. Please include more previous date about OTX1 and OTX2
- methods: OK
- Results: See 2. experimental design.
- Discussion: There are a lot of introuction in the discussion. In the discussion section you must compare your date with other manuscripts from other groups.
- Conclusion: Please include only the conclusion, exclude speculation.
Experimental design: About the experiments;
1) It is missing bright field microscopy in all microscope images. Please include in
- Figure 1
- Figure 2
- Figure 5
- Figure 6
- Figure 7
- Figure 8
2) For OTX1, the staining is present in all cells and usually the co-locacization is always observed. Is it right?
3) The image of  western-blot for OTX1 and OTX2 is not clear as described in the figures 9B and D.
4) The citokines must be quantified by elisa.
5) Please, include IL-17, IL-23 and TGF-beta. Colite is associated to TH17 response and Th17 was not evaluated.
6) Please correct, in mRNA you detect pro-IL1beta.
Validity of the findings: The authors used only one methodology to prove the finding (microscope). If used other techniques as Flow-cytometer will increase the strength of the manuscript.
Additional comments: Dear authors.
The manuscript is interesting, however, it is missing mechanisms.
1) What is the function of the increased of OTX1 and OTX2 after DNBS treatment?
2) What is the function of OTX1 superimposable with inducible nitric oxide synthase (iNos)? and nNOS?
3) Is it the increase of OTX1 and OTX2  associated to increase of citokines? Which?
4) Is the increase of OTX associated to microbiota? It will be interesting to treat mice with antibiotics.
5) If you prime cells in vitro with LPS, is it possible to induce the same mechanism?


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: HOMEOPROTEIN OTX1 AND OTX2 INVOLVEMENT IN RAT MYENTERIC NEURON ADAPTATION AFTER DNBS-INDUCED COLITIS
Review round: 1
Reviewer: 3

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The paper is interesting
I suggest the authors to add in the introduction other drugs used for intestinal inflammatios, see  these papers:

Jo A, Yoo HJ, Lee M. Robustaflavone Isolated from Nandina domestica Using
Bioactivity-Guided Fractionation Downregulates Inflammatory Mediators. Molecules.
2019 May 8;24(9).

Szebeni GJ, Nagy LI, Berkó A, Hoffmann A, Fehér LZ, Bagyánszki M, Kari B,
Balog JA, Hackler L Jr, Kanizsai I, Pósa A, Varga C, Puskás LG. The
Anti-Inflammatory Role of Mannich Curcuminoids; Special Focus on Colitis.
Molecules. 2019 Apr 19;24(8).

Pagano E, Romano B, Iannotti FA, Parisi OA, D'Armiento M, Pignatiello S,
Coretti L, Lucafò M, Venneri T, Stocco G, Lembo F, Orlando P, Capasso R, Di Marzo
V, Izzo AA, Borrelli F. The non-euphoric phytocannabinoid cannabidivarin
counteracts intestinal inflammation in mice and cytokine expression in biopsies
from UC pediatric patients. Pharmacol Res. 2019 Nov;149:104464.

Pagano E, Capasso R, Piscitelli F, Romano B, Parisi OA, Finizio S, Lauritano A, Marzo VD, Izzo AA, Borrelli F. An Orally Active Cannabis Extract with High Content in Cannabidiol attenuates Chemically-induced Intestinal Inflammation and  Hypermotility in the Mouse. Front Pharmacol. 2016 Oct 4;7:341.

Capasso R, Orlando P, Pagano E, Aveta T, Buono L, Borrelli F, Di Marzo V, Izzo AA. Palmitoylethanolamide normalizes intestinal motility in a model of  post-inflammatory accelerated transit: involvement of CB₁ receptors and TRPV1 channels. Br J Pharmacol. 2014 Sep;171(17):4026-37.

The manuscript would benefit from inclusion of introducing/bridging sentences between the individual parts of the "Results" that explain the logical order and rationale for the experiments

In the Discussion, the Authors should highlight the possible clinical significance of their findings


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

Input:
Title: THE HISTORY OF MESOWEAR: A REVIEW
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is clear and unambiguous. It provides an extensive review of the literature on mesowear over the past 20 years. It summarize the history of mesowear and its evolution with the description of the different methods that were designed.
The literature references are exhaustive and I could not identify any missing work.

It is very useful to have access to the raw data. Besides providing the original data, it is also a source of information to find mesowear data for species or taxa.

Minor corrections:

Lines 46-46. Who did use “meso-wear” to refer to age determination technique? I checked Grant (1982) and I did not see it. Grant is using “MWS” but not meso-wear. Please add the references where “meso-wear” is employed.

Line 84. The reference Rivals et al. (2007a) is missing from the list. Additionally, there is no “2007b” in the text, so it should be cited as (2007).

Line 85. At the end of the sentence, I would suggest to add “lifetime, especially for brachydont taxa” because the signal is much more stable in hypsodonts.

Line 92: The two variables, OR and CS, were combined not only to simplify, but because the two variable are not fully independent. They convergence towards the grazing end of the dietary spectrum, i.e. blunt teeth have low relief. This is important when the two variables are used for statistical tests.

On Figs. 4, 5, 7, 9 it would be useful to have the N on the figure or the caption. To know how many papers belong to each category.

Captions for Fig. 2 and 3 are inverted in the pdf.

The list of references in Annex 2 needs to be checked carefully as I could spot some mistakes:
- Many Latin names of species are not italicized.
- What are the papers cited at the beginning of the list?
- The reference Diana P, Juha S……. (2020) is wrong. These are the first names of the authors. The correct list of authors is: Pushkina, D., Saarinen, J., Ziegler, R., Bocherens, H., 2020.
Experimental design: The methods are well explained and I could not identify any missing information. Most of the sources are adequately cited (see minor mistakes in section 1).
Validity of the findings: The finding are valid and provide important points for future research on mesowear.
Additional comments: No additional comments


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

Input:
Title: THE HISTORY OF MESOWEAR: A REVIEW
Review round: 1
Reviewer: 2

Output:
Basic reporting: This manuscript is a welcome review on mesowear analysis. As rightly stressed by the author, there are now currently many variations of the original method and it is difficult to get a good overview of the pros, cons and field(s) of application of each variation. This manuscript does just that, in a clear and concise manner.
The manuscript is well-written: the structure is logical and the wording is clear.

The intro and the background do explain the relevance of the study, and reference to previous work adequately.
However, two topics have been excluded from this review, and I believe they deserve some space:
- Mesowear as an environmental proxy - there have been quite a lot of discussion and debate around the signal provided by mesowear: is it a dietary or an environmental proxy? I do not think this debate is closed, but in any case, this topic must be addressed in the introduction.
- The author does not provide enough background and clarity regarding the different scales of wear analyses and how they relate to each other: how microwear affects mesowear and how both affect hypsodonty? Are the different methods just about different dietary signal durations, or are the wear agents and processes different at different scales? There is a lot at play here, and the few sentences on this topic (lines 40-45 and 230-232) are too vague and are mixing many concepts in an ambiguous manner. Please expand on this topic, in the introduction and discussion, potentially linking it to my previous comment.

Raw data are shared as appendices.

The figures are OK, but I am one of those persons having a strong opinion against pie charts, especially with so many categories (e.g. Fig. 4 is simply unreadable). A simple Google search “pie charts why not” will provide a lot of clear arguments why pie charts are most of the time suboptimal and should be replaced with bar charts. Some might say it is a matter of taste, but this is only partly true. Hopefully the author and/or editor will be convinced by all the blog entries and articles discussing the topic, and the revised version will replace pie charts with bar charts.
Experimental design: The methodology is described in enough details (pending some minor comments – see “General comments”).
The review is, as far as I can tell, exhaustive and unbiased. The sources are correctly cited. There are just a few places where pages are not cited for quotations (see “General comments” – comments #16 & 31).
Validity of the findings: I think the results are interesting per se. But I also believe that the author could make more of it, provide recommendations for current use, as well as more avenues for future improvements (see “General comments” – especially comments #19-20, 33-34, 37).
Additional comments: In this section, I detail some minor comments, following the manuscript’s structure.

ABSTRACT
1)	Line 10: I am not a supporter of the royal “we”. This is more stylistic than anything, but I would recommend simply writing “I” in this sentence. Passive voice is also OK.
2)	Line 16: repetition of “present”; maybe “The present study reviews in detail…”

INTRODUCTION
3)	Line 28: typo in “Introduction”.
4)	Line 30: although not everybody agrees, the most common term for the 3D microwear method is “dental microwear texture analysis” or “DMTA”. Rather than two out of many case studies, I think that citing reviews will be more suitable here (e.g. Ungar 2015, Calandra & Merceron 2016; DeSantis 2016; Green & Croft 2018 for some recent ones).
5)	Line 32: “… about a specimen’s and, by extension, a species’ diet”.
6)	Lines 40-45: some references are switched between the “phytolith” (Xia et al. 2015, Merceron et al. 2016…) and “grit” (Lucas et al. 2013, Sanson et al. 2007…) proponents. Please check and correct.
7)	Lines 45-50: this topic deserves its own paragraph.
8)	Line 45: “… tooth wear patterns have also been…”
9)	Lines 49-50: “… this technique is solely applied to estimate age…”
10)	Lines 51-52: mesowear is not only performed with the naked eye, as shown in Table 1 and on lines 105-110. Please clarify here.
11)	Lines 53-55: I recommend merging this sentence with the sentence on lines 57-59; it is a bit repetitive as is.
12)	Line 55: the original method is applied only to the M2 (Table 1).
13)	Lines 55-57: I recommend moving this sentence to lines 66-71. This will at the same time help explaining to the non-expert what “attrition-based/abrasion-dominated wear patterns” are.
14)	Line 59: replace “length” with “duration”.
15)	Line 60: “… at the evolutionary scale…”.
16)	Lines 63-64: the quotation is missing a reference (including page number).
17)	Line 79: it is not clear who “the authors” are here.
18)	Line 82: please add references to support the claim that “rudimentary dietary assumptions are sometimes made using a single tooth”.
I think the wording “as complete specimens are rare” is somewhat misleading. To me, a “complete” specimen would be a full skeleton/skull/mandible…; I guess “well-preserved specimens” is more appropriate here. But my interpretation might be wrong.
19)	Lines 82-85: does it then mean that the diet is not stable through the lifetime? If it is indeed not, then it has huge implications for mesowear analysis. Please expand.
20)	Line 90: OR seems redundant because it is correlated to CS. But are there exceptions, or in other words, how good is the correlation? I think this would be the space for a critical, rather than purely descriptive, review.
21)	Lines 96-98: it is not clear to me whether this is mesowear I or II. Based on Table 1, it is apparently both, but I do not see how it can be both… Is it just that the authors extended and applied both methods at once?
22)	Line 121: “promote enhance”; this is redundant, probably a typo.

METHODS
23)	Line 127: maybe “recorded” is a more appropriate word than “cited” here.
24)	Line 131: “… n=211 publications were analysed.”
25)	Line 132: “… PhD and MSc theses…”
26)	Lines 140-141: how can species be “listed with multiple entries within a single study”, if it is not because of localities and time periods (which would mean “various” diet)?
27)	Lines 145-146: I find the terms “extant*-**” make it difficult to remember what they mean. What about “extant_archaeo” and “extant_fossil”, or something similar?
28)	Line 159: I do not understand what the “percentage of the species’ main diet” is. Can you please elaborate here?

RESULTS
29)	Lines 166-169: refer to the naming used in Fig. 5a, so that the link between text and figure is easier to follow. See also comment #27.
30)	Lines 171-173: there is a simple explanation for this pattern: categories other than browsing/grazing/mixed are taxon or paper-specific.
31)	Lines 180-182: add a reference, with page, for this quotation.

DISCUSSION
32)	Line 202: please define what you mean with “coarse” scale.
33)	Lines 212-215: is this a recommendation for future studies? Is this the methodology that seems the most promising, based on the present review? If yes, I recommend emphasizing it, and expanding on it (including the possible limitations of using this methodology over any other, or of using only one methodology…). As it is, this review is mostly purely descriptive; I argue this here would be the missing synthesis.
34)	Lines 216-217: because there is no independent proxy for diet, this metric cannot discriminate between stability of diet and reproducibility of the method itself (as mentioned lines 155-157), both aspects being very relevant to the future development of the methodology. However, this ambiguity is somewhat forgotten in the discussion. The reproducibility aspect should be stressed again here, interpreting the same data from a different perspective.
35)	Line 239: “… seem to confirm…”
36)	Another avenue for future development concerns automation and objectivity of the method. This relates somewhat to comment #34. I know that some have tried to automatically score mesowear from photographs, using image processing algorithms. Yet, as far as I know, no automatic method has been proposed, probably because the gain is not worth the time needed to develop it. Still, this remains a potentially very important development for future studies, especially for “increasing reproducibility and reducing repeated measures” (lines 220-221).

TABLE and FIGURES
37)	Table 1:
- The table could be made much more useful/practical in restricting the column “scores” to include only true scores (like for the original mesowear, unlike e.g. Mesowear I - Adapted for Lagomorpha), potentially giving more details (e.g. Mesowear II “quantitative mesowear”), and adding a column “diet” or “interpretation” of the scores.
- Additionally, I think some methods have been replaced by newer ones. Therefore, an extra column about which method replaces which one could make this table even more useful.
- It should be explained why the method Mesowear I – Adapted for Conodonta does not have scores (i.e. it is not truly mesowear).
38)	Fig. 1 (legend):
- I recommend moving “from Taylor et al. (2016)” to the end of the legend.
- Capra hircus has no mention of cusp height (hypsodont, right?)
- Never heard the term “hyperhypselodont”. A horse tooth is not hypselodont (ever-growing) anyway, even though the root forms late during ontogeny. Maybe “hyperhypsodont”?
39)	Figs 2-3: I think the legends have been switched.
40)	Fig. 7b: I do not understand what the author means with “Grey markers indicate multiple species (and multiple diets)”, which also means I do not understand what the bulk of the figure shows. I also recommend choosing another pattern (color) for mixed diets.
41)	The numbering of the figures does not follow the order in the main text. I recommend some reorganization:
- Figs 5a+7a+6a+4 --> new Fig. 4
- Figs 5b+6b --> new Fig. 5
- Fig. 7b --> new Fig. 6

I hope these comments are constructive and will help improving this manuscript.


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

Input:
Title: PROTEOMIC SIMILARITY OF THE LITTORINID SNAILS IN THE EVOLUTIONARY CONTEXT
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors present an interdisciplinary study, bridging the fields of proteomics and evolutionary genetics, to study the evolution of several species from the gastropod family Littorinidae. The manuscript is clearly structured according to PeerJ standards, with a well-written introduction that provides the necessary background. While I cannot comment on the literature on proteomics and the study taxa, the remaining literature is well referenced and relevant.

I have two comments to improve the manuscript with respect to basic reporting:
1)	While the figures are relevant and of high quality, Fig. 1A and B should be improved with respect to the placement of statistical support values on the trees. Specifically, support values are not clearly placed at their respective branch or seem to be missing (e.g. the posterior probability for the branch leading to L. arcana / L. compressa in Fig. 1B). Moreover, the manuscript would be easier to follow for readers who are not familiar with the study taxa if you would add labels for genera and subgenera to the trees (Fig. 1A and B, Fig. 2).
2)	The English language is overall clear and unambiguous, but the manuscript would benefit from improving the grammar, for example in lines 35, 73, 98-101.

Further, I have a few minor suggestions to improve the text:
-	Lines 382-388: Moving this section to line 376 would make the whole paragraph easier to follow for the readers.
-	Line 309: L. marisrubri should be L. melanostoma.
-	Line 491: You refer to Fig. 1, but this should be Fig. 2.
Experimental design: The authors present original primary research, combining the analysis of newly generated proteomics data with already published DNA sequencing data. The research question is well defined and relevant to the field of evolutionary biology and the authors make clear that their research fills a knowledge gap regarding the evolutionary history of littorinid snails.

I commend the authors on the overall study design of comparing proteomics with DNA sequencing data analyses. It is great to see the use of statistical similarity measures to compare trees estimated from proteome and DNA sequencing data. However, the chosen methods are solely based on similar clustering or pairwise distances between tips of the trees, and none of the methods take tree topologies or branch lengths into account. I would like to refer you therefore to the following paper that evaluates the performances of different tree distance measures to choose an additional statistical measure: https://academic.oup.com/sysbio/article/64/2/205/1630737

Further, I have the following minor suggestions how to improve the methods descriptions:
1)	Line 238-241 (and throughout the manuscript and figures): For readers who are unfamiliar with littorinid snails it is sometimes difficult to follow which species belong to which genus or subgenus, as not all species names used in the figures are used consistently throughout the manuscript. In this particular sentence, it is not clear which species belong to Littorina (Neritrema) and Littorina (Neritrema / Littorina).
2)	Line 253: Please refer to the supplement 1 where the parameters are described more in detail.
Validity of the findings: The authors have provided all underlying data. Newly generated presence/absence proteomics data has been provided as supplemental material and the sources of the analysed published data are available. While I cannot review the quality of the proteomics data, I have a few comments on the interpretation and discussion of results obtained from DNA sequencing data.

The DNA sequencing data analysed in this manuscript consists of two mitochondrial and one nuclear locus. I am missing a discussion on the possibility that the phylogenetic tree based on these loci does not correspond to the species tree (or genome-wide tree), which is the basis to the discussion of the findings from proteomics data. For example, in lines 402-404 you mention that L. obtusata and L. fabilis were shown to share mitochondrial haplotypes. Such a pattern might have been caused by hybridization which could have affected the topology of the tree based on DNA sequencing data.

Also, you mention in line 287 that low statistical support comes from unstable clustering pattern. I am missing some further discussion of this finding, especially keeping in mind that the phylogenetic analysis of DNA sequencing data was only based on three markers which might not contain enough substitutions to resolve this part of the tree. Alternatively, gene flow might explain the low posterior probabilities at these branches (see above).

Further, I noticed that the two Littoraria species are clustering as sister group to the two Echinolittorina species in the DNA sequencing data, but as sister group to all Littorina species in the proteomics tree. This is only mentioned in lines 303-304, but missing from lines 276-277 and other sections. I would suggest to discuss this difference between the two topologies.
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: PROTEOMIC SIMILARITY OF THE LITTORINID SNAILS IN THE EVOLUTIONARY CONTEXT
Review round: 1
Reviewer: 2

Output:
Basic reporting: I read this manuscript with great interest. I am a molecular systematist, specialised on working with DNA sequences, but I am always open to other forms data that can inform us about relationships of particularly closely related taxa. As such, I wanted to be convinced that proteomics could be an interesting source of such information. As DNA sequence data is what the majority of researchers are using, I am sure I am not alone in this.

Unfortunately I was not convinced, rather I was left somewhat confused by what the data actually is and how it was used. Keep in mind that I (along with the majority of the readers of an article such as this) have little experience with proteomics, how the data is collected, and what it actually is. I elaborate on this below.
Experimental design: The research question is clear, the potential results interesting, but the reader needs to be convinced, is this an approach that I would like to use?

The authors state that their approach is comparable to AFLP, RFLP, RAPD, etc. Fine, but what is the data actually? Table S0 suggests that there are almost 800 characters for which there is presence/absence data. But looking at the names of the characters, it would seem that for many characters we are actually talking about different forms of the same protein (Ah1, Ah2, Ah3 etc). Is that right? If so, I cannot find anywhere how many individual proteins were used to collect data. Surely much less than 796. Does coding each form of a protein as an independent character have an effect on results? What if each protein was coded as a multistate character? Maybe such things have been discussed in the literature earlier, but as I said, I am unfamiliar with that.

A couple of hundred proteins must be a small fraction of all the proteins found in the specimens at the time of sampling, how have exactly these proteins been chosen? Again, you need to convince somebody who is frustrated with DNA data and is looking for another source of phylogenetic information for their problem, but is not an expert in the field of proteomics.

For phylogenetic analysis, the dataset is reduced to a distance matrix based on the Jaccard index. This is then made into a dendrogram using UPGMA. Any particular reason why UPGMA is used? Why not a neighbour joining algorithm? Could UPGMA be the reason why E.mil+E.mar do not come out as sister to L.mel+L.ard?

For the molecular analysis, the authors state that MrBayes is used in a standard fashion, yet they show an ultrametric tree. MrBayes does not give an ultrametric tree under standard analyses. How have the authors made the tree ultrametric? This is not clear at all from the text.
Validity of the findings: The authors compare their proteomic data to DNA sequence data from three loci, totally unrelated to the proteins. My initial thought was, what if we had the DNA sequences for each of the proteins used in the study, would they be as informative as the proteomic data? Now it is not really a fair comparison, unless the point is to say that one can relatively cheaply do the proteomic analysis as suggested by the authors, compared to doing a whole genome sequence to find the DNA sequence of the same proteins. Can the authors comment on this in the manuscript?
Additional comments: In general, I found the study to be interesting, but the manuscript should be revised to make it clearer why such data could be useful for others. Write it for the ignorant (like me), this study is not aimed at specialists in proteomics, it is aimed at the systematist interested in their organisms and their relationships.


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: PROTEOMIC SIMILARITY OF THE LITTORINID SNAILS IN THE EVOLUTIONARY CONTEXT
Review round: 2
Reviewer: 1

Output:
Basic reporting: The language in the article has improved very much compared to the previous version. The authors will find minor language corrections in the attached PDF to further improve the language.

Also, I have made suggestions for population genomics, phylogenetics and phylogenomics literature to be cited in the attached PDF.

The figures have been improved with respect to the placement of statistical support values and taxon labeling. However, the resolution is not ideal and should be increased.
Experimental design: I only have one minor comment on the methods section, where the parameters used in the phylogenetic analysis using MrBayes should be included (see PDF).
Validity of the findings: No comment
Additional comments: I commend the authors for the improvements to the article compared to the previous version. I attached a combined PDF of the main document and the supplementary material with minor comments to 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: PROTEOMIC SIMILARITY OF THE LITTORINID SNAILS IN THE EVOLUTIONARY CONTEXT
Review round: 2
Reviewer: 2

Output:
Basic reporting: I thank the authors for their revision, which makes the manuscript now much clearer, I enjoyed reading it! And it has intrigued me about using proteomics to look at closely related species and species boundaries.
Experimental design: All looks good now.
Validity of the findings: The revised manuscript is now much clearer on the use of proteomics for looking at species level questions.
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: LINC00958 AND HOXC13-AS AS KEY CANDIDATE BIOMARKERS IN HEAD AND NECK SQUAMOUS CELL CARCINOMA BY INTEGRATED BIOINFORMATICS ANALYSIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1) Abstract has some cell line acronyms like NPEC2 25 Bmi-1, would be helpful to names of them. Some couple gene symbols need also to be elaborated.

2) References seems to be old, can you replace them with last 10 years references?

3) English and grammar seems reasonable to me.
Experimental design: 1) Authors state that "In the present study, The Cancer Genome Atlas (TCGA) database was used to identify 68 differentially expressed genes (lncRNAs, miRNA and mRNA) between HNSCC and adjacent 69 normal tissues." Why this number sample size chosen?

2) Where the samples from same batch?

3) I don't see sample ids from TCGA database, can authors please provide them?

4) Cluster analysis for heatmaps looks crowded, can authors separate them into different figures instead of different panel?

5) The threshold of >1.5 was chosen significant, can authors explain the reason or the reference to do that?

6) Can authors validate expression of two significant genes with RT PCR if access to tissue samples?
Validity of the findings: The data on which the conclusions are based in an acceptable discipline-specific repository.
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: LINC00958 AND HOXC13-AS AS KEY CANDIDATE BIOMARKERS IN HEAD AND NECK SQUAMOUS CELL CARCINOMA BY INTEGRATED BIOINFORMATICS ANALYSIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Dear authors,
Thank you for your hard work with this paper.
New biomarkers in SCC are strongly needed to be discovered.
The English language  is fluent. However you should change some abbreviations.
In literature there are head and neck cancers you should remove headneck phraze and change.
Also you neet to use one type of abbreviation (title, 16,41).
You should check references list and improve (e.g.221-222).
Raw data and figures are good shared.
Differences in title should be made, because you are testing only nasopharyngeal cell lines, so it have to be mentioned.also source of both cell lines is missing.
Please change manuscritp and write about nasopharyngeal cancers according to WHO guidance.
Experimental design: In the TCGA base there are tissues from oral cavity, oropharynx and laryngeal sites ( Nature volume 517, pages 576–582 (29 January 2015), but aren’t any from nasopharyngeal site. You have to mention about the orgin/location of tested squamous cell carcinomas and cell lines.
There is no marker to divide if squamous cell carcinoma is arising from lung or head and neck region, however in is unclear if there are different mechanisms of RNA action, please mention that.
Please write about orgin of cell lines.
Validity of the findings: Findings are interesting, but  it is unclear if you can compare nasopharyngeal orgin with other orgins of squamous cell carcinoma.
What would you think, would be appropriate to compare squamous cell carcinoma of lung and head and neck due to lnc/micRNA ?
Even during clinical trials nasopharyngeal cancers are excluded from treatment for other locations.
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: OPTIMIZATION OF AERATION ENHANCED SURFACTANT SOIL WASHING FOR REMEDIATION OF DIESEL-CONTAMINATED SOILS USING RESPONSE SURFACE METHODOLOGY
Review round: 1
Reviewer: 1

Output:
Basic reporting: The author made nice effort to improved the soil soil washing performance by 12-25% through incorporation of air bubbles into the low concentration surfactant soil washing system.
Experimental design: Although the experimental process was completed in about one year starting from soil sampling to their drying and grinding and then contamination with diesel, but written well and can be understand easily.
Validity of the findings: The results shows interesting improvement in the remediation of diesel contaminants from soil. These results are interesting, but i suggest to improve the validity of this technique, to use this technique on large scale as the soil of the near by areas to oil refineries, processing plants and oil field are highly contaminated with hydrocarbons.
Additional comments: I read with much interest this manuscript reporting on " Optimization of aeration enhanced surfactant soil washing for remediation of diesel-contaminated soils using Response Surface Methodology". Looking to the environmental issues related to the soil contamination. The author made nice effort to improved the soil soil washing performance by 12-25% through incorporation of air bubbles into the low concentration surfactant soil washing system. Overall, I found the manuscript interesting, with certain novelty over the existing state of the art. Based on the details given in the manuscript, I believe it can be improved still and can be brought up to meet the expectations from a paper in Peer J. Besides, there are some issues which need to be answered by the authors in this version of the manuscript. Also, state of art needs to be defined better and some key references are missing. The language also needs careful revisions. Thus, the manuscript as it is written now, the work needs minor revisions. Any other comments for improving the manuscript are-
1.	Although Figure 1 explains the soil washing scheme, but that is mentioned as Fig 1. He manuscript quality can be improved by adding suitable graphical abstract.
2.	Introduction: The introduction of the manuscript looking long. Concise the text to bring the impact of the need.
3.	In the introduction part on page 2 the wrote that “Different physical, chemical, and biological remediation techniques are commonly used to treat the petroleum polluted soils; these methods aim at destroying, modify them into harmless byproducts and reducing contaminant concentration”. Authors may check this recent paper to strengthen this aspect- 2019, Environmental perspectives of interfacially active and magnetically recoverable composite materials–A review Science of the Total Environment 670 (2019) 523–538.
4.	It is suggested to insert more relevant recent reference citations at appropriate instances for better readership.
5.	The grammar of the article should be re-checked. There are many mistakes.   English grammar must be improved, especially concordance between subjects and verbs.


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: OPTIMIZATION OF AERATION ENHANCED SURFACTANT SOIL WASHING FOR REMEDIATION OF DIESEL-CONTAMINATED SOILS USING RESPONSE SURFACE METHODOLOGY
Review round: 1
Reviewer: 2

Output:
Basic reporting: This manuscript integrated the additional physical mixer (i.e., air bubble) with the conventional contaminated soil washing using surfactant solution. The quality of manuscript is within standard both English and design of experiment. The outcome also presented the possibility of this technology in the real application.
Experimental design: This manuscript could be divided into 3 sections which were surfactant selection, process optimization by CCD and technology comparison (with and without aeration). In my opinion, the author should have additional figure which showed the overall of this work. This should make the reader easily understand the flow of this manuscript.
CCD is the useful RSM since it could reduce the number of experiment. However, this manuscript used a large number of factors (time, pH, air flow rate, surfactant concentration and agitation) which might not be suitable for CCD and very hard to explain the results. It should have a screen experiment for important factor and its boundary prior to CCD such as sequential experiment or Taguchi method. Did the author conduct the preliminary study?
In this research field, liquid to solid ratio is very important factor. Please explain why the author did not consider this factor. The author used 20 mL/g as the fixed liquid to solid ratio. Several works attempt to reduce liquid to solid ratio due to the cost of operation (i.e., surfactant and infrastructure). Generally, they operated between 3-10 mL/g.
Validity of the findings: Did the author conduct the replication? If so, please add standard deviation in the revised manuscript.
Additional comments: -	There were several mistake according to space between number and unit (Line 173, Line 175). Please check the whole document the correct this issue.
-	In table 3 please check the unit: Min vs min, Mg, mg
-	Applying aeration improved the diesel removal and surfactant usage. Did it economic feasible? The author mention about applying temperature in soil washing was uneconomical (Line 228).
-	I would like to encourage the author for soil characterization, especially soil texture (composition of sand, silt and clay). This soil texture significantly affected to the diesel removal performance.
-	The author used UV spectrophotometer at 225 nm to evaluate the diesel concentration (Line 175) Please add the reference. Diesel is the group of long chain hydrocarbon compounds not a single chemical. Did the simple UV spectrophotometer provide the good results? Is there any interfere from dissolved organic matter in soil?
-	The author should report the final diesel concentration in washed soil and compared it to the standard.


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: OPTIMIZATION OF AERATION ENHANCED SURFACTANT SOIL WASHING FOR REMEDIATION OF DIESEL-CONTAMINATED SOILS USING RESPONSE SURFACE METHODOLOGY
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: I am appreciated to your effort in revising this manuscript.


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

Input:
Title: AN EFFECTIVE SURVEY METHOD FOR STUDYING VOLANT SPECIES ACTIVITY AND BEHAVIOR AT TALL STRUCTURES
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper satisfies most basic reporting requirements though it is unclear whether or not raw data will be shared.
Experimental design: See comments to author
Validity of the findings: See comments to author
Additional comments: The paper seeks to assess the effectiveness of two remote sensing methods to monitor flying animals in the vicinity of wind turbines, and based on results, suggest recommendations on their application.  The concept has merit as continued growth is expected in wind energy development and methods of minimizing risk to flying animals are still under development.

The paper would benefit from matching the scope of its impact as described in the introduction to the actual data gathered.  On lines 79-80, the paper purports to determine best practices for assessing behavior of flying animals at tall structures, but only one kind of structure is studied (turbines), one remote sensing technology is varied (thermal imaging), and one variable is examined (distance from the base of a turbine).  Identifying “best practices” for the application of even a single technology would identify and explore a far greater list of issues including different sampling strategies and times of night (and times of the year), detection range for different sized objects and how those interact with background conditions (a concern described in the paper), the region of coverage (e.g., whether or not to image the rotor swept area), methods of quantification and statistical analysis, the competing benefits associated with different kinds of thermal imaging technology, and how all these may vary with conditions.  (Regarding that second to last point, the usefulness of a given thermal imaging technology will be based on a variety of often competing factors including field of view, specific operating frequency/wavelength, cost, and dynamic range and sensitivity.)  Likewise, lines 82-83 imply multiple technologies will be examined when only thermal imaging is varied; this is the heart of the paper and the intro and discussion should be structured around exploring the effects of thermal imaging flying animals at different ranges from turbines.

There are some concerns with methods, and the discussion in general is brief and could be much more exploratory.  These are described in greater detail in the line-specific comments below.

Ln139.  The field of view would increase with distance from the base, so an accurate comparison would require controlling for this difference such that the same field of view was being assessed across distances.  The effect would be an even greater difference between sampling near the turbine v. further away.  Best to correct in analyses, but at least mention this caveat in the discussion.  Also, why was the rotor swept area not included in the field of view when that is the area impacting the vast majority of flying animals?

Ln159-160.  Why not leave the recording equipment on throughout the 200 min time frame?  How were time stamps synchronized across the recording devices?

Ln168.  What is the significance of 8 cm?  Does this refer to the long axis of biological targets?

Ln169.  A bird has a head, body, and wings.  Was the primary morphological difference patagium (bat) v. tail (bird)?

Ln171-172.  Acoustic verification seems subject to considerable uncertainty.  The acoustic source could be from a bat outside video coverage (unless these were highly directional mics, which seems unlikely).  Moreover, video range presumably far exceeded the max range of acoustic monitoring (45 m), so only lower height targets stood the chance of being verified this way.  And what was the max distance a bat-like target could be identified in thermal and NV data?  It’s important to know given the role this equipment plays in determine risk to flying animals from rotors that begin some 40 m AGL.  Likewise, the max resolvable height for insects is much lower, especially to resolve wings (Ln173).

Ln173.  I cannot resolve a bird-like target in the figure.

Ln174.  Like the concept of an ‘undefined’ or ‘unidentifiable’ category, but why call it a ‘possible bat’ if it could also be a possible bird or possible invertebrate?  Leave as undefined or unidentified throughout.

Para beginning Ln177.  How were these scored?  One person?  Did a second individual blindly score a subsample as a validation?  Were NV and thermal imagery scored separately to avoid bias?  BTW, avoid referring to thermal imagery/video/data as thermals, that term is unclear and has other meanings.

Ln185.  Seems ‘sweeping’ would be challenging to identify from video….how do you know the wing touched?

Ln191-195.  Like reduction to simpler categories.

Ln206.  Use of KW test suggests data does not satisfy assumptions for a parametric test.  These things should be stated.

Ln207.  What is a Games Howell test and what is its specific purpose here?

Ln217.  146 trials in six nights is greater than the number of trials possible in six nights given the 12 10-min trials per night mentioned on Ln159.

Ln216+.  Much of the next 30 lines or so could be placed in a table and made much easier to read and compare.

Ln239.  See comment Ln217.

Ln244-245.  Is this the point of saturation of the camera, or is it that the background temperature is indistinguishable from that of the target.

Ln250.  “per hour”…but data were gathered in 10-min blocks?

Ln252-257.  Mix of parametric and nonparametric among these four test results?

Ln275-278.  So greater likelihood of uncertainty from data gathered closest to the target.  Why would that be?

Ln289-290.  The background is likely the same at 2 m as it is at other ranges (or nearly so).  A combination of spreading loss over greater distance and limited dynamic range of the camera would cause weaker thermal signals from flying animals to merge with background.

Ln291+.  What if data were gathered later in the evening giving the tower time to cool?  Might bat-like targets be more detectable?  Might a camera with more dynamic range (higher bit resolution) increase the likelihood of resolving subtle differences in temp between a bat and background be it the sky, cloud, or turbine?

Fig5 seems to offer little.  Maybe let this result stand on the text alone.


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: AN EFFECTIVE SURVEY METHOD FOR STUDYING VOLANT SPECIES ACTIVITY AND BEHAVIOR AT TALL STRUCTURES
Review round: 1
Reviewer: 2

Output:
Basic reporting: This study evaluates two approach to generating video imagery for studying bat behavior associated with wind turbines and other tall structures. The following are my comments on the manuscript. Thanks for letting me take an early look at this manuscript. I enjoyed reading it.

I would see the focus of the study as follows: (1) compare and contrast two approaches to generating video imagery of bats at tall structures; and (2) develop and use a taxonomy of behaviors for studying bat behavior associated with these structures. The current manuscript does a very good job of describing the technical methods used, but in my opinion, the discussion of behavior and placing the work in a broader context could be improved.

I don't quite feel like these authors provide a thorough review of the literature related to how bat researchers have tried to use video imagery to study bats at wind energy facilities, and I don’t feel like the authors thoroughly discuss how their approach fits into this long-term line of research. I also feel that the discussion is too short and doesn’t provide enough detail in comparing this work to the other research that has occurred, or  consideration of how the behavioral results here relate to results observed by other researchers.

I would recommend that PeerJ consider publishing this manuscript after a revision.
Here are some specific comments for the author’s consideration:
-	Line 43: Consider defining what is meant by a “tall” structure. How tall?
-	Line 54: What specifically is meant by “population-level implications”?
-	Line 66: Consider defining “deterrent”. Some readers will be unfamiliar with this term.
-	Line 67: Likewise, consider defining “operational minimization”.
-	Line 75: Consider citing the Cryan et al. (2014) paper here, along with the others.
-	Line 83: Consider using “animals” instead of “objects”.
-	Introduction, general: I would encourage a thorough review of the behavioral ecology literature related to flight behavior in bats. There is a rich literature here that goes largely un-cited.
-	Introduction, general: consider restricting the purpose and focus of the paper to studying flying bats, then returning to the broader question of volant animals in the (longer) discussion.
-	Line 95: consider including common names for each species.
-	Lines 109-110: consider briefly describing the physics of these two approaches. For example, what wavelengths of light are they documenting, and any other important differences so readers who are unfamiliar with these technologies have a better sense for how they compare to each other.
Experimental design: The study design strikes me as reasonable and well considered.
Validity of the findings: I think this work will be of broad interest to bat and bird ecologists and others. The results appear to be well documented and presented.
Additional comments: Keep up the good work. I'll look forward to seeing this in print in the not-too-distant future. See above for specific recommendations.


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 FIELD-BASED INVESTIGATION OF BEHAVIOURAL INTERACTIONS BETWEEN INVASIVE GREEN CRAB (CARCINUS MAENAS), ROCK CRAB (CANCER IRRORATUS), AND AMERICAN LOBSTER (HOMARUS AMERICANUS) IN SOUTHERN NEWFOUNDLAND
Review round: 1
Reviewer: 1

Output:
Basic reporting: This is an interesting study that uses field experiments and observations to test the hypothesis that the invasive European green crab could prohibit lobster from entering traps and may therefore be responsible for recent declines in lobster catch.  The authors conclude that this is indeed possible, but I have substantial reservations about this conclusion.  I outline my concerns, as well as other suggestions for the manuscript, below.
1)	This is a very long paper.  The length could be reduced by removing portions of the Introduction that are not really pertinent.  For instance, there is a lot of information on genetics and temperature tolerance of green crabs, on their impacts on eelgrass beds, and on previous eradication methods that, while interesting, is not pertinent to the topic of this paper.
2)	The Discussion of the paper is FAR too long!  I’m not sure that it is necessary to separately discuss each and every part of the study.  Discussing the study as a whole instead would be much more concise.

Minor comments
1)	Line 127 – remove “are”
2)	Lines 265-269 – description of Poisson GLMM not necessary.  This is a standard ecological test for count data.
3)	Lines 334-336 – explanation of prop.test is redundant with explanation above
4)	Perhaps give the number of traps deployed and the numbers of hours of video footage in the Methods section rather than in the Results.
Experimental design: 1)	The researchers used video cameras to observe interactions in and around lobster traps, but they simply used ambient light to do this.  Given that crustaceans are often more active at night, it may be that many interactions were not observable.  What impacts may this have had on the results of the study?
2)	Lines 198, 223 – I recognize that the green crab is an invasive species, but collecting individuals for “disposal on shore” seems potentially ethically problematic.  How were these individuals disposed of?  The authors state that the project was approved by the University Animal Care Committee, but I think it is still worth ensuring that animals were disposed of humanely and weren’t just thrown in a dumpster in a plastic bag to die slowly in the heat.
3)	SCUBA surveys – if one diver pulled out the transect line right before the other diver did the survey along the line, it is likely that the activities of the first diver would have disturbed crabs and lobster, causing them to either hide or leave the area.  These surveys may therefore have underestimated the abundance of animals.  And these artifacts, if they occurred, could have been species-specific.
4)	Lines 274-276 – Perhaps a multi-model comparison using AIC would be a more robust method of identifying the best-fitting model.
Validity of the findings: The premise of this study is that green crabs are reducing the catch of lobsters by interfering in some way in or around the traps.  The authors conclude that crabs inside traps reduces lobster entrance into traps.  However, I have fairly serious concerns with this conclusions for the following reasons.
This study was conducted in an area where lobster fishing had just been closed, and thus the lobster densities were presumably relatively low because of the previous fishing.  Yet this study caught a total of 326 lobsters and just 6 green crabs in traps.  Further, few free crabs were observed in 452 h of video (line 390-291).  This does not provide much evidence that green crabs are entering traps.  This suggests that the high density of crabs tethered in the traps for the experimental treatments was much higher than the density of crabs expected to enter lobster traps normally.  Thus, the impact of the tethered crab treatments on lobster catch here is likely hugely overestimated.
Further evidence that crabs are causing a problem in lobster traps comes from the fact that there was no impact of crab presence on the success of small lobsters in entering the traps.  Interactions between crustaceans are strongly determined by individual size.  We should expect therefore that crabs would have the largest impact on the smallest lobsters.  The fact that there was no impact on these small individuals suggests that crabs are not the problem here.  I think that the findings here that fewer large lobsters entered traps with crabs simply reflects the incredibly (and unrealistically) high density of crabs (7 adult crabs in an area much smaller than 0.25 m2) in a confined area.  This will of course lead to an increase in aggressive interactions both between crabs and between lobster and crabs.
Finally, there was no evidence here that crabs depleted bait in the traps, even when they were stocked at these crazy high densities.  So the mechanisms was instead likely direct aggressive interference as lobsters entered the traps.  But the fact that all predation attempts observed were of lobster eating crabs, further suggests that crabs are not deterring lobster in general (i.e., aggressive interference from crabs at reasonable densities would likely have weak impacts on lobsters).  The most likely scenario for a lobster encountering a trap is to have no crabs inside (based on the observation that few crabs entered traps here).  The next most likely scenario is to have crabs inside, but at a much lower density than used in this experiment.  In this case, results here suggest that the lobster would view the crab as a prey item, not as a problem or a reason not to enter the trap.
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: A FIELD-BASED INVESTIGATION OF BEHAVIOURAL INTERACTIONS BETWEEN INVASIVE GREEN CRAB (CARCINUS MAENAS), ROCK CRAB (CANCER IRRORATUS), AND AMERICAN LOBSTER (HOMARUS AMERICANUS) IN SOUTHERN NEWFOUNDLAND
Review round: 1
Reviewer: 2

Output:
Basic reporting: I love the premise of this study, as it addresses an urgent question for the management of green crabs on the east coast in a very applied way, however the quality of the writing is not suitable for publication. The introduction in particular needs to be rewritten or significantly restructured so the relevant pieces of information are grouped together, rather than scattered throughout. I am also unsure as to why there is so much focus on phenotypic plasticity and genetics in the intro when it is neither alluded to or directly addressed in the remainder of the MS. There are also places where the authors are not clear about their meaning. I have provided some examples below.

I would suggest that the authors use “green crab” rather than “crab” in the introduction (and throughout), to distinguish between green crab, rock crab, and crabs generally.

Suggest removing ‘tethering’ from the title, as this is not a formal tethering experiment.

1.	I suggest re-phrasing the concluding sentence of the abstract (lines 41-43), for clarity. For example: Our results suggest that while there is a relationship between in-trap crab density and trap effectiveness, it is not linked to the non-native / native status of the crab species.
2.	Lines 52-53: Specify that you mean adult tolerances here (vs larval)
3.	Lines 56-62: Examples of the impacts detected would be helpful here (rather than Lines 90-94). Specify that you mean impacts on the east coast of North America (as impacts elsewhere may be different).
4.	Line 65: Specify the native range
5.	Lines 101-111: This paragraph is out of place, as the impacts of green crab were already discussed above (so this section should be moved up). Following the preceding impacts, you need to expand on the issues with lobster here, including competitive interactions with green crabs.
6.	Lines 127-128: Can you explain what about them isn’t understood in more detail? The preceding paragraph outlined a number of studies that did look at lobster-crab interactions.

The discussion has some similar issues.

1.	Lines 440-458: Why is it unclear? It doesn’t seem all that biologically surprising if a large rock crab is already in the trap that you wouldn’t get small lobsters entering. This is potentially very interesting from the perspective of naivete on the part of the lobsters. Are they recognizing a native competitor/predator but not an invasive one?
2.	Lines 527-538: From this, I don’t understand how significantly fewer entry attempts by lobsters on green crab stocked traps does not also cause a significantly lower catch of lobsters?
3.	Lines 564-566: Do you mean lobster abundances were consistent for all traps for each deployment?
Experimental design: I appreciate the direct and very applied methodological approach used and commend the authors on how many hours of video they scored! I have no fundamental issues with the experimental design but there are two large oversights in the analysis that would need to be addressed before publication: set depth and body/claw size.

Increasing depth, even over a few meters, could result in large changes in the species composition and size of decapods (e.g. larger crabs found at depth). Given the traps are set over a large range of depths, I would like to see depth accounted for in some way, preferably statistically as a co-variate in the models.

Similarly, the body size (and more importantly to interspecific interactions, the claw size) of decapods is crucially important in determining the outcome of agonistic interactions (e.g., Baillie & Grabowski 2018, Ecology). While the authors do give some consideration to “large” vs “small” lobsters, the issue of size is not well explored statistically, despite it being a primary explanation for their results in the discussion. I think there are a number of ways size could be analysed more thoroughly. For example, measuring the claw size (or perhaps meral spread) of decapods interacting on video to see if the larger decapod always wins. This might also provide some information about how tethering may have affected the results.

There are also some clarity issues to resolve in the methods/analysis sections and figures/tables.

1.	Lines 174-175: Were these depths reflective of where pots are set to catch commercial/recreational lobster?
2.	Line 185: Were depths randomly assigned or haphazard? Are depths standardized against mean low water?
3.	Line 199: In the same location?
4.	Line 222: Specify whether notch-notch or point-point measurements were used.
5.	Line 228-229: Unclear. Three dives were done per deployment, one per pot? Or were all pots surveyed three times per deployment.
6.	Line 253: Figure number?
7.	Line 298: Negative-binomial?
8.	Line 315-316: If the transect was done over 25 m moving away from a baited trap, how are they independent? I would expect the bait to attract crabs and lobsters, leading to higher densities as you move towards the trap?

Figure 5: Suggest the points be made different shapes and smaller.

Figure 6 and 7: Suggest the captions needs to provide more explanation (e.g. that this is from the video data analysis, what is going on for deployments 5/6, how specifically these two figures differ).

12 figures in the main MS is overwhelming. I recommend paring the figures down to those that pertain most directly to your main findings/hypotheses, and creating a supplementary file for the remainder.

What does ‘standard trap’ mean in Table 1? Check for consistency in treatment names throughout figures.
Validity of the findings: If the authors can statistically address the effects of depth and body size/claw size on their results, then I would likely consider their findings valid.
Additional comments: I think the use of video to understand interspecific interactions of these species is a fantastic approach to a really important, applied, question. Beyond its applied aspect however, it is also a great approach to studying the behavioural ecology of invasive and native decapods (as the authors mention, video provides a very fine scale for making observations). However, the authors state several times in the discussion that their findings are 'unclear'. I think using the invasion ecology and behavioural ecology literature more extensively would provide some clarity.


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 FIELD-BASED INVESTIGATION OF BEHAVIOURAL INTERACTIONS BETWEEN INVASIVE GREEN CRAB (CARCINUS MAENAS), ROCK CRAB (CANCER IRRORATUS), AND AMERICAN LOBSTER (HOMARUS AMERICANUS) IN SOUTHERN NEWFOUNDLAND
Review round: 1
Reviewer: 3

Output:
Basic reporting: Per comments below, there are some issues with the reporting, especially relating to the need to be more concise and clarify methods and results. Also, the discussion appeared to me to be a really long results section rather than a synthesis of information and how it relates to other published work.
Experimental design: I think the design is fairly sound. I was a little uncertain of why the authors tethered the crabs when they were doing video capture.
Validity of the findings: I think validity is fine. The way presented needs revising per above and below.
Additional comments: General Assessments:
This MS presents a study of the potential impact of green crabs on the capture of lobsters in Newfoundland. Given the crab’s general impact in the region, this represents an important avenue of study, particularly given the decline of lobsters in the region and the potential role that green crabs may play in that decline or lobster recovery. I think this MS is worthy of publication, but there are some issues that need to be resolved prior to publication. First, the introduction has some mischaracterizations and missing information regarding the background information of the green crab invasion in the region (and throughout Nova Scotia). Second, I think it may be better to transform the hypotheses into questions. I found the hypotheses hard to understand at times, and in some cases, I was having trouble following the logic behind them. They also did not always have a clear rationale about why the hypotheses were formulated (one example being a hypothesis for green crabs versus rock crabs affecting catch of lobsters). Third, a lot of the methods and results could be more concise. There was quite a lot of wordiness throughout the manuscript, and it made it difficult to follow at times. I think organizing around your questions/hypotheses is helpful, but the descriptions could be shortened significantly. In line with this, there are too many figures – these should also be condensed. Finally, the discussion to me felt more like a longer version of the results – there was very little return to what was presented in the introduction. For example, to me, there seemed to be arguments made in the introduction related to temperature tolerance in green crabs, but this is never returned to in the discussion. Is there something about that which is of value to this study? Generally, this paper could be written in a way that helps it serve as a contribution to the general understanding of the impacts of green crabs worldwide, but there was very little of that in the discussion – it was very focused on just explaining the findings in this study, rather than how the findings of this study link to other findings and what the implications could be to our understanding of this globally invasive crab.

I have other minor suggestions in the appended .pdf. I also have specific comments about certain sections which are in the appended .pdf but also copied and pasted below.

--Third paragraph of introduction: Missing in here is the discussion of the potential for neutral processes in the green crab invasion between the two lineages... this is discussed in Pringle et al. (2011), Darling et al. (2014), and Lehnert et al. (2018). These should be introduced in here as alternatives (or potentially also at play) to the temperature tolerance hypothesis.
--Introduction 4th paragraph: “These populations contain both southern and northern genotypes and genetic analysis indicates a close match to the more cold-tolerant, northern populations (Blakeslee et al., 2010; Roman, 2006).” This is a misrepresentation of these papers to go along with the hypothesis of temperature tolerance. What the genetic data tell is that the Newfoundland source was from Nova Scotian populations that are associated with shipping between Nova Scotia and Newfoundland. There was nothing about temperature in there and there is no way to even make that conclusion using those data. This sentence needs to be revised for accuracy. Moreover, the Roman paper did not look at the Newfoundland data because there were no green grab populations detected in Newfoundland at the time of the sampling for that paper.
--Methods: Tethering. In general, I'm not really clear on the point of tethering if you were going to video the crabs anyway. It seems to have added an extra variable to have to deal with. Why tether? More explanation is needed here.
--Discussion: “It is unclear why rock-crab pre-stocked traps captured fewer lobster than unstocked traps.” This seems to suggest you had an a priori idea that rock crab stocked traps would inhibit lobsters less, but I don't see any clear reason for that. Are you suggesting lobsters are more likely to avoid green crabs than rock crabs? If so, there needs to be some kind of evidence presented to support that. It may simply be a density dependent effect, regardless of crab identity.


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 FIELD-BASED INVESTIGATION OF BEHAVIOURAL INTERACTIONS BETWEEN INVASIVE GREEN CRAB (CARCINUS MAENAS), ROCK CRAB (CANCER IRRORATUS), AND AMERICAN LOBSTER (HOMARUS AMERICANUS) IN SOUTHERN NEWFOUNDLAND
Review round: 2
Reviewer: 1

Output:
Basic reporting: This version of the paper is much improved.  The authors have substantially clarified their points and have removed extraneous material in the Introduction.  Much appreciated!  The Discussion is still excessively long, but it is better.
Experimental design: The experimental design has been clarified, and I'm happy enough with it - though I still contend that AIC is a superior way to select the appropriate model as compared to stepwise model selection techniques.
Validity of the findings: No comment.
Additional comments: No additional comments


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

Input:
Title: A FIELD-BASED INVESTIGATION OF BEHAVIOURAL INTERACTIONS BETWEEN INVASIVE GREEN CRAB (CARCINUS MAENAS), ROCK CRAB (CANCER IRRORATUS), AND AMERICAN LOBSTER (HOMARUS AMERICANUS) IN SOUTHERN NEWFOUNDLAND
Review round: 2
Reviewer: 2

Output:
Basic reporting: A lot of effort has clearly been made and the improvement to the Introduction is particularly noticeable. However, it is my opinion that the writing still needs significant work to effectively communicate the findings of this study. A lot of really interesting and relevant angles remain under- or un-explained. I think this is partly (perhaps largely) due to a need for better organization/flow in the writing.

My specific comments hopefully clarify the areas where I feel the authors need to expand or re-organize, but in general the link between the impact of an invader on a very important commercial fishery deserves more attention, as does the behavioural ecology.

Specific comments and suggestions on the reporting
Review the use of crab vs crabs throughout for consistency. Are you using ‘crab’ as both the singular and collective noun, or crab (singular) and crabs (collective)? Same for lobster/lobsters. For example, there’s a switch between these uses in line 37 where the lobsters (collective) eat crab and lobster (also collective). It is either “the lobsters ate crabs and lobsters” or “the lobster ate crab and lobster”.

Review the order in which methods and results are presented. In most places the green crab treatment is described first, then the rock crab, but this is reversed in places (e.g. line 285).

Clarify the distinction between legal/sublegal vs. adult/juvenile lobster (especially in the Discussion).

23: Move ‘marine’ up to the beginning of the sentence (to distinguish from terrestrial invaders, which probably don’t have an impact on marine biodiversity), could also add ‘native’ in front of biodiversity. However, this paper isn’t about biodiversity really, its about the impacts of an invader on a commercial fishery. That would be a more relevant opening.

25: Newfoundland, Canada

26: Specify that lobster are native to the region

34-27: Combine 1 and 2 for brevity/clarity (“Regardless of the species of crab stocked, crab presence reduced the total number…. compared to the empty control traps.”)

39: I am skeptical of the word “newly” here. What defines a new invasion and why does it matter that it is new? There is no substantive discussion of why the invasion being new is relevant to the findings (here or on the actual Discussion).

46 (paragraph): The assertions made here should be backed up with examples from the literature, to better make the case for linking invasion ecology research to fisheries management. There are interesting examples across taxa where a marine invasive was responsible for the decline of a fishery (e.g. Mnemiopsis ledyi, Indo-Pacific lionfish, etc). The latter would go a long way to making this paper conceptually interesting to a larger invasion ecology audience and not just us green crab nerds!

55: Remove “finally”

60: Remove the apostrophe in 2000s

63: Can be severe (they are not in all cases, eg. South Africa, Australia).

61-71: Why emphasize the eelgrass thing and not their impact on fisheries through direct species interactions (which is what the paper is about)? I would suggest expanding on their impact as a predator and/or competitor. The indirect effect of green crabs on ecosystems via eelgrass loss is important, broadly speaking, and deserves mention but much less relevant than the direct impacts in this context.

77: I think ‘traditionally’ here may undersell the commercial importance of lobster to Nfld?

80: “…presence of the species” instead of invasion here.

83: Most readers won’t understand or know where Fortune Bay is or if/why it matters. Either identify and reference on Figure 1, or generalize the statement (e.g ‘ongoing expansion of the species into still-productive lobster fishing grounds…”).

90: Conclude with something like “However, no studies to date have examined how these species interact outside the lab”. When you think about it, it’s a huge and important step to take what we know from the lab and move it into the field. I think this deserves emphasis, here and in the Discussion.

92: Presumably there have been some studies on lobster recruitment in Newfoundland? The central argument between intraspecific population dynamics of lobsters vs interspecific interactions between lobsters and crabs as the reason for declining catches is rather scattered throughout and the population dynamics part needs more support.

91 (paragraph): I think this paragraph is quite methods-heavy for the intro.

111: I think the “ie.” part here is unnecessary

137: ‘zodiac’ is a brand name (Zodiac) and would likely not be recognized as a colloquialism for the type of boat by many/most readers. Change to rigid-hull inflatable boat (or whatever it was).

144: Specify that this is 50 m horizontally, not vertically.

147: Here it says crabs, but could that not mean rock crabs?

148: In accordance with Memorial University’s animal care protocol?

155-159: While I have no problem with the stocking densities, they should be better justified here for the sake of clarity.

206: Move this sentence up to the end of the preceding paragraph (line 201).

202-208: A reasonable effort was made to address the issue of size differences I put to the authors in the first revision. However, none of that made it into the paper? The method used to determine the size of claws for crabs involved in the 60 predation attempts should be described here, and should also be mentioned in the Results and Discussion.

240-244: This doesn’t need to be re-stated in the Methods as this justification is (or should be) in the Intro already.

Results (overall): I think it should be explicitly stated which fixed effects were dropped and which remained in the final model for each of the GLMMs (only done for SCUBA results?).

Section 3.1: I am confused by the way the information contained here is broken up into paragraphs. The topic sentences don’t match the subsequent content and makes it hard to follow.

312: Clarify – I can’t tell this means “(i.e., excluding….)? As is, it reads as though the authors did count the lobsters entering the sides?

Discussion (overall): In general, there is repetition of the results in the discussion (eg. line 365-366), and there is repetition within the Discussion itself (e.g line 456). It may be worth considering structuring the Discussion based on the hypotheses presented in the Intro, rather than the experiments from the Methods, to reduce repetition?

The whole Discussion still needs work to make the findings and their biological importance clear. As suggested by another reviewer, this paper could slot nicely into the larger green crab impacts literature, especially given its commercial fishery implications, but to do this the authors need to go beyond restating and explaining the findings of the paper in isolation. While this has been improved on this revision, I agree with the reviewer and feel there is a ways to go to fully accomplish this.

372 (paragraph): I feel like there is a better way to present this limitation. There are average or high stocking densities, right? So it is less likely that the results have underestimated the effect.

397: The figures also show this as the catches often/consistently asymptote (Fig 5).

407: Does not need to be re-stated

412: This paragraph is a useful example of some of the things that could be improved from a writing perspective. First, the topic sentence doesn’t really clarify what this paragraph is about as the next sentence is about something completely different and arguably more important. Second, the paragraph is a re-statement of results but there is no discussion provided. For example, if bait depletion has been put forward as an explanation for lower lobster catches demonstrating why that isn’t the case is important! Could there be a biological explanation (is there evidence in the literature that green crabs don’t feed when stocked at density because of competition, or they don’t like the bait provided, etc). Or is it an experimental design problem and, if so, what could be done in future studies to better answer the question of bait depletion?

496-501: This assertion needs to be much more clearly articulated. I draw the opposite conclusion from this. Ie., that there was a failure to observe what was actually a very large population of green crab in the first year on SCUBA.
Experimental design: Sections 2.6 – 2.8: Going back to my previous comments, I am still not wholly satisfied with the treatment of depth in this paper.

BH: Increasing depth, even over a few meters, could result in large changes in the species composition and size of decapods (e.g. larger crabs found at depth). Given the traps are set over a large range of depths, I would like to see depth accounted for in some way, preferably statistically as a co-variate in the models.

Authors: We added clarification of the depth ranges at which traps were deployed (3 to 19 m mean ± 1 S.D. = 9.52 ± 4.27 m , as measured at low tide). Within each deployment, the traps were deployed at depths within a few meters of each other. Therefore, within deployments, differences in depths did not influence our response variable.  (Lines 135-136)

The clarification on depth range is useful. However, I don’t think the authors can say that differences in depth did not influence the response variable without better (statistical) justification. Although the deployment number is used as a random effect in the relevant models, that still wouldn’t address within-deployment variation in depth. A few meters change in depth would definitely affect the size and number of decapods caught in other systems, so the authors need to provide evidence that it does not matter in this system. Given that the actual depths are known I can’t see a reason not to do this statistically? Since the authors use stepwise model selection, adding depth as a covariate from the start seems the most straightforward to me. However, maybe simpler models (catch ~ depth and size ~ depth) compared to a null model would work (as a supplement even)?
Validity of the findings: As before, I think the findings are interesting and valid. They did the best they could with the available data to address the issues of size I brought up previously (although that work should go into the paper!). But I feel depth still needs to be addressed.
Additional comments: This paper has a lot of potential, but the presentation of the paper falls short of what I would expect for scientific publication. I realize that this is a high standard, but I believe the science done here is worth the effort.