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: SQUEEZING WATER FROM A STONE: HIGH-THROUGHPUT SEQUENCING FROM A 145-YEAR OLD HOLOTYPE RESOLVES (BARELY) A CRYPTIC SPECIES PROBLEM IN FLYING LIZARDS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Language and structure are appropriate overall (though note exceptions detailed below). Figures are appropriate. Raw data is supplied, though I'd also like to see the HTS data available on Dryad.
Experimental design: Research is original and the research question is well defined. However key details and justification of the methods are not provided by the authors, which mean that I cannot recommend the manuscript be accepted/published in its present state (see details below).
Validity of the findings: I have no major issues with the conclusions of this study. I think the data, though admittedly scarce, are ultimately adequate to address the research question.
Additional comments: Summary:

The authors use a variety of approaches to obtain mtDNA from the holotype specimen on D. cristatellus, a flying lizard, in order to verify its taxonomic validity. The authors successfully obtain limited data from the holotype, and find that it is genetically distinct from closely related congeners while being closely related to a recently collected specimen also identified as D. cristatellus. Thus, the validity of D. cristatellus is supported. The authors also comment on the possible implications of the methodological difficulties they encountered for future studies using non-ideally stored specimens, and indeed much of the paper is focused on this aspect of the work.

I don't have any any major criticisms of the results of this manuscript or their interpretation (insofar as sufficient detail has been given to allow me to assess them). However, given the methodological focus/pitch of the paper there is a distressing lack of detail and critical examination of many of the steps undertaken, particularly with regard to the HTS. As my background is in HTS, and particularly HTS as applied to ancient/degraded samples, this is the area of the paper that I am best equipped to assess and many of my comments/criticisms reflect this. In my view, there is too little documentation and too many unexplained observations (e.g. extremely high human contamination in sample and extraction control) for me to recommend the acceptance of this manuscript in its current form.

Main issues:

1. Overall lack of details in the method section, particularly regarding the HTS and PCR on the D. cristatellus holotype.

2. Splitting of information between Methods and Results that makes comprehension extremely difficult, as the reader is forced to flick back and forth between the two to actually figure out what the authors have done. All of the information pertinent to the Methods should be moved from the Results section to the Methods section.

3. Unexplained and distressing human contamination in the HTS data, and lack of acknowledgement of the ancient DNA laboratory involved...

Detailed comments:

Line 104 - "For reasons that we will describe in a subsequent paper"
Though it may not ultimately be critical for interpreting the results of this paper, I would prefer that the authors give some preliminary justification for this decision. What assurance is there that this subsequent paper will actually be published, or that the reader of this will be able to find said paper? Something like "Based on X (Unpublished Data and/or Pers. Comm.) we instead..." might be more appropriate. The following sentence (beginning Line 106) regarding the type locality of D. fimbriatus does nothing to clarify this issue for me, though I think that is the intent.

Line 106 onwards - I'm confused about whether the D. fimbriatus mentioned is D. fimbriatus sensu McGuire et al. or D. fimbriatus sensu Manthey. This issue persists in the final paragraph of the introduction where I'm unclear on whose taxonomy is being used. The primary aim of the paper seems to be verifying the distinctness of D. cristatellus, which does not appear to be affected by this taxonomic issue. So why do the authors not leave unraveling the D. fimbriatus/punctatus/abbreviatus mix-up for their subsequent paper where it can be dealt with fully and explicitly, and thereby save the reader of this paper any undue confusion? I do understand that the authors are trying to "future-proof" this manuscript, but as written currently I think it just muddies the water for someone unfamiliar with the detailed taxonomy of the group (i.e. me!).

Line 190 - What ND2 primers, PCR recipe, and cycling conditions were used for this amplification? I'm surprised that the authors were able to amplify human DNA using primers designed for reptile ND2 (it would be less odd for the conserved 12S/16S genes) and I'm not aware of any universal primers for ND2. If the authors were not using taxon-specific primers (or indeed, if they were targeting too long a fragment) then it is not surprising that the amplification failed. Perhaps the annealing temperature was too low? Insufficient detail is given here for a reader to assess the reasons for failure. Similarly, in this paragraph the authors mention "low" DNA yield but don't quantify this or even state what method was used to quantify the DNA (though I note this this is later reported in the Results section).

Line 198-199 - Which ancient DNA lab exactly? As far as I can see they aren't even listed in the acknowledgements... Did the lab specifically ask not to be named?

Line 231-232 - What parameters were used in SeqPrep?

Line 233-234 - The authors note they assessed the quality of sequences using FastQC, but we are left to guess whether quality was good or bad because the authors make no statement about this. I assume that the quality was OK...

Line 255-257 - How many unique reads? What proportion of the reference was covered? What was the average read depth? What was the average read length?

Line 264-267 - How were the contigs for the D. cristatellus holotype generated? Why map all of the other sequencing reads against those contigs instead of mapping everything against the Draco reference you built using the data for TNHC56763 (including the D. cristatellus data)?

Line 280 - I strongly suggest that the authors also make their HTS data available on the Dryad repository.

Line 290-309 - This whole paragraph is basically a repetition of information in the Methods, so I think this paragraph should be removed and any non-redundant information moved to the relevant section of the Methods.

Line 313-316 - I have to believe there is some mistake here. The authors have 538,995 reads of which 29,790 are assigned to human. That means 5% of the DNA molecules in the DNA extract are human! Orders of magnitude more than the actual target lizard DNA. Is it possible that there was some mix-up of barcodes with a human DNA library run in parallel? Because otherwise this represents an extremely distressing level of contamination in an ancient DNA laboratory. It could perhaps be written off as contamination of the sample (maybe through handling by museum staff) except that ~3% of molecules in the extraction control also appear to be human! I would appreciate a statement from the authors on this issue, and should also hope that the aDNA lab is currently investigating this further and reviewing their protocols as this level of contamination could easily compromise any mammal research (not just human) being undertaken in the lab.

Line 325 - Could the authors please report mean read length and depth for the D. cristatellus holotype data?

Line 362-364 - This transition almost certainly represents post-mortem deamination of the template molecule (as ubiquitously observed in ancient/museum/degraded samples). Given the low number of reads sequenced in the present study, any transitions observed in the D. cristatellus holotype should be viewed with suspicion.

Line 376-389 - Does this refer to published work? Or is this another reference to the authors' upcoming publication? Either way, this information would have been more appropriate in the Introduction, with a brief summary at the beginning of the Discussion. Why are specific hypotheses only being outlined in the Discussion?


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

Input:
Title: SQUEEZING WATER FROM A STONE: HIGH-THROUGHPUT SEQUENCING FROM A 145-YEAR OLD HOLOTYPE RESOLVES (BARELY) A CRYPTIC SPECIES PROBLEM IN FLYING LIZARDS
Review round: 2
Reviewer: 1

Output:
Basic reporting: I would like to thank the authors for their improvements to the manuscript, particularly the addressing of unpublished data/methods has much improved the paper.

I believe I may not have been clear enough concerning the reasons behind exhaustively reporting the BLAST hits. I completely agree that the mammal, human and bacterial contaminants do not pose any significant problems and are commonplace (DNA from domesticated/human associated animals is often encountered in these experiments). However, showing (by means of a BLAST list) that you receive significantly more hits on Iguana (Anolis+Draco) compared to other totally random animal (sub-)orders (e.g. Lamniformes) would actually add further support that your data are genuine and not some artefact. I leave it up to you if you want to incorporate this idea.

With respect to the holotype data; I would like to see the average total library length vs the average mapped length for both the capture and the shotgun sequencing experiments. These data are a good indicator whether or not your data are genuine, normally the overall libraries are expected to be longer due to recent/human contaminants in comparison to the genuine DNA that was fragmented.

With regard to removing the "total" and "%" columns in the table. I respectfully disagree that readers will be aware of the effect of evolutionary rates on gene divergence, part of your audience (think morphological systematics and field biologists) may not fully appreciate the biases in these numbers (also note that pairwise nucleotide distances in ND2 are about 75% more than in COI simply due to differing rates). I therefore strongly suggest that you include a line along the lines of "the divergence estimates are affected by varying evolutionary rates and are therefore indicative. the divergence estimates do however strongly indicate [your conclusion]".

With regard to ethanol preservation both your paper as well as that of Ruanae and Austin make an intersting observation that deserves mentioning. Note that Ruanae and Austin only looked at a very limited 4-5 alcohol preserved specimens, with an average age older than the formalin fixed specimens. Altogether there is not a lot of evidence for superior formalin DNA preservation over that of ethanol preservation. There are far more papers that suggest alcohol preservation outperformes formalin in terms of DNA preservation though (https://doi.org/10.1016/S0002-9440(10)64472-0 https://dx.doi.org/10.1186%2F1742-9994-5-18 https://doi.org/10.3897/zookeys.196.3130 just to pick a few), this therefore deserves some balanced reporting backed up by references.

Please also correct the value mentioned in line 344 so that you compare ND2 vs ND2 values rather than “mitochondrial genes” vs ND2 values; please also mention the values for D. punctatus.
Experimental design: please see the basic reporting section
Validity of the findings: please see the basic reporting section
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: SQUEEZING WATER FROM A STONE: HIGH-THROUGHPUT SEQUENCING FROM A 145-YEAR OLD HOLOTYPE RESOLVES (BARELY) A CRYPTIC SPECIES PROBLEM IN FLYING LIZARDS
Review round: 2
Reviewer: 2

Output:
Basic reporting: No additional comments.
Experimental design: No additional comments.
Validity of the findings: No additional comments.
Additional comments: The authors have satisfactorily addressed most of the questions and concerns I raised in my original review.

I have only three remaining comments, only one of which (the third) really requires any action or response from the authors. Otherwise, I think this manuscript is suitable for publication in PeerJ in its current form.

1)
The last paragraph of the introduction remains extremely dense, with binomials and authors - that the casual author will be completely unfamiliar with - flying thick and fast. At the end of the introduction I am still left unclear as to the exact taxonomic hypotheses being tested. The authors give an excellent and clear description of all competing hypotheses, however it does not appear until the beginning of the discussion. If it were me, I would simply move the first paragraph of the discussion to the end of the introduction. This straightforward change requires no additional rewriting, but would allow the reader to "catch up" if they became lost in the dense taxonomic discussion at the end of the introduction and gives them clear context for the Results section. I understand that this comes down to a difference of opinion and style, so I'll leave the resolution of this issue to the editor's discretion.

2)
The authors partially addressed my concern about human contamination in the DNA extractions. Indeed it's quite plausible that the contamination in the sample itself comes from handling by museum staff/researchers. What remains unclear to me is why the extraction blank control should exhibit similarly high levels of contamination. Regardless, I agree with the authors that it is highly unlikely to have impacted the results of their study, as no lizard contamination was detected. It's simply a curiosity that I hope the ancient DNA lab in question is monitoring or following up on independently, ~3% human DNA in a blank control seems a lot.

3)
Line 288-299 - "after combining the data from 2 different libraries (prepared identically) from the same extract"

In the Methods section (a) (Lines 229-230) the authors describe only one library being created from the holotype sample (and one from the extraction blank control). However, in the line quoted above they refer to two different libraries from the same extract. Could the authors please make clear exactly how many libraries were created and sequenced from each sample/control, and make sure this is consistently reported throughout?


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: TOBACCO RATTLE VIRUS-INDUCED PHYTOENE DESATURASE (PDS) AND MG-CHELATASE H SUBUNIT (CHLH) GENE SILENCING IN SOLANUM PSEUDOCAPSICUM L.
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript needs through English language editing.
Experimental design: •	Text at many places are ambiguous e.g., L90-92, L133-34 also check overall for the grammatical errors.
•	Proper terminology should be used e.g., L88, steam sterilized should be replaced with autoclaved.
•	Age of the plant should also be mentioned in L90
•	Sampling at L94 is not clear. Five different plants and three biological replicates?
•	L97- what tissue was used?
•	Name of the supplier is needed in L99
•	Homology-based cloning section can be expanded with the mention of closely related species used and gene IDs used for the cloning. Mention if degenerate primers were used. Also, mention the template used for PCR and number of cycles.
•	Some of the headings are not conclusive e.g. L130
•	L131, where was PDS inserted?
•	L131-137 needs improvement for better clarity
•	Reference is needed in L110, L143
•	Mention of kit or method is needed in L112
Validity of the findings: •	Overall clarity in writing is needed e.g., L162-64. Some of the headings need improvement for the better conclusion e.g., L161, L220. Check for the capital and small letter placement
•	Mention the name of the species used for homology in L162
•	I don’t find any figure for 3’RACE result
Additional comments: Abstract
Information is sufficient but improvement in writing/language is needed for better clarity and readability.

Introduction
Information and citations look conclusive but writing requires improvement for better understanding e.g., line 17.

Figures
Figure 1: legend can be expanded with details of methods used and with details of the template used and a number of cycles.
Figure 2- details are needed for each figure like if A) is RT-PCR and B) is qRT-PCR.  Needs better sentence framing for the clarity. Mention number of replicates for RT-qPCR
Figure 3- expand the legend with tissue sample used for the experiment and number of replicates used
Figure 4- expand the legend with details of input values and number of replicates
Figure 5- what is 1,1 and 2,2 in the figure? Expand the legend
Figure 6- check for the spelling mistakes in legend. Legend is confusing, what is the difference in C and D figures. Expand the legends with the methodology details
Figure 7 can be merged with figure 8
Figure 8- labels on figure do not match with the legend for 8A. also mention the age of tissue used and a number of replicates for qRT-PCR.

Other points that need attention
•	How was the consistency of silencing in plant lifespan?
•	Was silencing in other tissue parts of the plant found?
•	Did silencing inherit to the next generation?


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: TOBACCO RATTLE VIRUS-INDUCED PHYTOENE DESATURASE (PDS) AND MG-CHELATASE H SUBUNIT (CHLH) GENE SILENCING IN SOLANUM PSEUDOCAPSICUM L.
Review round: 1
Reviewer: 2

Output:
Basic reporting: English writing should be improved. L45, L47 the two viruses name should be italic. L61 A should be a. L63 RT-qPCR. L76 A blank before Thus. L80 correct provide to provided. L83-L84 delete the last sentence. L121 delete five. L132 -133 Eco should be italic. L137 DH5a should not be italic. L143 need reference.

Plant materials only cover the plant used in study. L90-95 should be introduced in each part of materials and methods.

L108 sequences of these genes should be attached.
L110 Primers should be as supplementary data.
L169 GenBank accession numbers should be given for these cloned genes.
L175-184 should be merged into next section. L182 delete the first the.
L261 The silencing rate is not clear. The authors should clear ow many plants were inoculated, how many plants were infected, and how many plants showed silencing phentotype.
Experimental design: The main purpose of this work is to report TRV could be used as VIGS vector in Solanum pseudocapsicum. However, the authors put much words on reference genes selection for RT-qPCR, though it is important for this plant. I suggest the authors to have more work to optimize the inoculation methods to improve silencing efficience, and try to silence one more gene for solid data.
Validity of the findings: I could not understand "The silencing rate was 26%". The silencing efficience should be shown in the result.
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: CENOZOIC ARIDIZATION IN CENTRAL EURASIA SHAPED DIVERSIFICATION OF TOAD-HEADED AGAMAS (PHRYNOCEPHALUS; AGAMIDAE, REPTILIA)
Review round: 1
Reviewer: 1

Output:
Basic reporting: The writing requires some major tune-up. See more detailed comments below.
Experimental design: The design and execution are competent.
Validity of the findings: Conclusions are generally supported by the data and analysis.
Additional comments: This is a very interesting study of a very interesting group. The data are substantial and the analysis is competent. My main issue with this manuscript is its presentation. Overall, the manuscript reads like a draft, rather than a polished final product. Much of the manuscript needs to be trimmed, smoothed and tied up. I have two relatively large comments and many small ones.

Major comments

1. The results of the mtDNA. The authors may choose to either re-analyze the data (with some addition or change to Solovyeva et al’s data) and present the results as new or present them only in discussion for comparison (remove all related sections in Methods and Results). This would include Figure 2, which is exactly the same diagram from Solovyeva et al. (2014).

2. For most tables and figures (including supplementary ones), more detailed titles/captions and explanations are needed. These tables and figure should be self-content (fully understandable without referring to text). For example, Table S5. All abbreviation should be explained. Also, are these variable sites from the entire dataset (including the outgroups) or among only the ingroup members? This makes a huge difference because this study included a large number of outgroups. The variable and informative sites could be mostly among the outgroup members and provide no information regarding the relationships among the ingroup members, which is the primary goal of this study.

Other comments:

Line 88 and Line 130. Number of species and the use of species names. Although the Reptile Database was cited, about half of the names used in this study differ from these in the database. This creates confusion. The Database may not represent the most authoritative conclusion, but it does include most recent published results and is a good place to start. I would like to suggest that the authors used the names from the Database as much as possible, with some modifications and additions. For example, P. hispidus can be P. versicolor hispidus and P. kulagini can be P. versicolor kulagini.

Line 108-115. The paragraph is one long sentence. The authors could choose to either delete the paragraph entirely, or provide a brief review of the history of the phylogenetic studies of the genus (and move some of the discussion to here, e.g. line 406-445).

Line 165-180. Outgroup selection. The inclusion of all the non-agamid species may not be helpful in resolving the phylogeny of the genus Phrynocephalus. Although the inclusion may help in providing more calibration points and allowing some discussion on Agaminae, it my cause more harm to the analysis than the benefits. I would suggest removing all the distantly related outgroup and limiting discussion beyond the genus Phrynocephalus (e.g. line 446-467, see below).

Line 186-205. These three paragraphs need to be re-organized. They are confusing. ML and BI can use the same partition scheme. Dividing the alignment into 12 partitions may not be the best choice (line 197; could be over-parameterize the model); allow a computer program (e.g. the new PAUP or PartitionFinder) to determine the best partition scheme.

Line 233. Using calibration points from outgroup carries a risk; it is well known that such use has a tendency to over-estimate the time of divergence. Thus, in discussion, such tendency should be taken into consideration.

Line 241-243. May provide a brief justification of using a seven-region scheme.

Line 266-268. The rooting designation: Technically correct but conceptually wrong. Should be rooted by all outgroup members.

Line 269-271. These numbers are important and the numbers in Table S5 are different from the numbers presented here. In particular, how many variable/informative sites when only the ingroup members are included? When outgroup were included, the numbers could be dramatically increased but the majority of them could be uninformative among ingroup members.

Line 273-281. In the method section, there is no description about how the mt data were analyzed. I was having the impression that the tree from Solovyeva et al was used and the mt data was not re-analyzed. If the data were re-analyzed, a corresponding section should be provided in the method.

Line 282-320. The phylogeny (Fig 2) is exactly the published figure from Solovyeva et al (2014). None of these is new, and therefore, this section should be completely removed or minimized.

Line 322-324. What are the methodological differences between the concatenated analysis (ML, MP, BI) and the BEAST species-tree approach? What does the congruence between the sets of methods imply? Can you include the mtDNA data as the 5th loci in the species-tree approach?

Line 328-331. As I suggested earlier, the authors should restrain themselves from discussing issues beyond the genus Phrynocephalus (in this case, the monophyly of Agaminae), because the sampling is not designed for addressing these questions.

Line 341-356. The detailed description of the nuDNA tree should be combined with the last paragraph (line 332-339).

Line 376-383. I would like to see the confidence intervals being reported here (in addition to the means).

Line 406-445. Much of the historical review can be reduced (and move to the introduction section).

Line 446-467. The authors should restrain themselves from discussing issues beyond the monophyly of Phrynocephalus. This paper is about the phylogeny of Phrynocephalus, not Agamidae, for which the sample is very limited. Delete points 1, 2, and 3.

Line 508-525. Comparison to Arnold’s (1999) morphological analysis is probably important. In addition to describe differences, potential explanation of the differences should be provided. Comparison to mtDNA-based genealogies can probably be moved to next paragraph.

Line 515-525. This section is irrelevant to the main objective and should be removed.

Line 624-778. This part of taxonomic review is long the thorough, and I am not sure what to recommend. On one hand, this information is very useful for taxonomist; on the other hand, the detailed discussion distract from the main focus, the phylogeny of the genus. The authors probably should limit their discussion on the validity of various species. It is best evaluated with extensive samples at the population level. With the current sampling, it is better to focus on high taxonomic level. For example, the versicolor species complex (line 761-778). With only 6 sequences (Fig. 2), it is not suitable to discuss the validity of several species. Studies such as Urquhart et al (2009) with more than 170 sequences are better positioned to explore these topics.

Line 797. Habitat and body size evolution. Is there any evidence from fossil records to corroborate the arguments?

Line 832. Biogeography discussion. How large are the confidence intervals of divergence times? Be aware that geological events are also hypotheses and often have alternative explanations. For example, the Middle Miocene Climatic Transition. A quick read of Flower and Kennett (1994) find “The early stage of this climatic transition from ∼16 to 14.8 Ma…”  and then “In the later stage from ∼14.8 to 12.9 Ma, …”. Clearly the transition is not as sharply defined as 14.8-14.1 Ma, rather, much longer.

Figure 2. This is exactly the same diagram from Solovyeva et al. (2014). It should not be presented as new results. Also, more explaination is required in the caption, for example, what are all the numbers? On the left, it should read “amino-acid sequences”.

Figure 3. Are these animal pictures proportional to their true size? Clade J, BI value: it is the only clade without a BI value. High BS value but no BI is unusual. Is it a topo? Groups G and I are not monophyletic. Why is sp. light blue? Shouldn’t be part of group J (orange)?


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: CENOZOIC ARIDIZATION IN CENTRAL EURASIA SHAPED DIVERSIFICATION OF TOAD-HEADED AGAMAS (PHRYNOCEPHALUS; AGAMIDAE, REPTILIA)
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is clear and well-written.
Background information is provided and literature references are complete.
The article is good-structured, with clear figures and tables.
Experimental design: The research is original and is within aims and scope of the journal
Research questions are well defined and relevant. The research substantially fill existing gaps in the knowledge of Phrynocephalus phylogeny.
The research is performed with high technical and ethical standards.
Methods are described with sufficient details and information.
Validity of the findings: Results are novel and interesting for herpetologists and other biologists working in the area of evolution of desert biota of Central Asia.
Data are robust and results are statistically sound.
Conclusions are well-stated and are linked to original research questions.
Additional comments: I have few minor comments.
1.	There is disagreement between abstract and body text concerning reconstructed substrate preferences of the common ancestor of Phrynocephalus. In the Abstract, it is written that “The common ancestor of Phrynocephalus probably preferred soft sand substrates”. However, in the body text this substrate is defines as “stabilized sand habitats with clay or gravel”. I would describe this type of substrate as loose non-differentiated proluvial sediments at mountain’s pediments. Please, correct.
2.	The use of geographic term “Middle Asia”. In the western tradition, this term is not used, and this region is named “western part of Central Asia”. In the Russian geographic tradition the term “Middle Asia” is used for Turan Deserts and neighboring southern mountains (Tienshan, Pamiro-Alay) but not for Kazakhstan. Authors use this term in some parts of the text (Introduction) for Turan + Kazakhstan and in other parts (Material and Methods, Results, Discussion) for Kazakhstan only, what is not correct.
3.	Areas used for biogeographic reconstruction (lines 235-246) are just listed, but not defined. Graphical presentation of these areas appears only in the Fig. 7. Please, define these areas in the text and change “Middle Asia” to “Kazakhstan” (see above).


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

Input:
Title: CENOZOIC ARIDIZATION IN CENTRAL EURASIA SHAPED DIVERSIFICATION OF TOAD-HEADED AGAMAS (PHRYNOCEPHALUS; AGAMIDAE, REPTILIA)
Review round: 2
Reviewer: 1

Output:
Basic reporting: Line 160-161. One sentence does not make a paragraph. Please merge this paragraph with the paragraph above.

Line 167-176. All the three paragraphs are single-sentence paragraph. Merge them into one paragraph.

Line 172 and elsewhere. Many comas (,) are omitted. Please pay attention and add. For example, line 172 after “inference”, line 179, after “subset”.

Line 180. Bootstrap does not evaluated “clade stability”. It evaluates “nodal support”.

Line 181. It is probably better to abbreviate “bootstrap” as “BSP” (for bootstrap proportion), as oppose to “BS”.

Line 201-203. Another one-sentence paragraph. Either merge it with others or break the sentence into two. There are many other instances of single-sentence paragraph. Please revise.

Line 204-207. Re-phrase. Nodes received BPP below 0.90 may be considered as “not well-supported”, but certainly are not “unresolved”.

Line 204 and elsewhere, consistency. Both “PP” and “BPP” are used for Bayesian posterior probability. Suggest using BPP.

Line 300. Awkward sentence. Sentence may read “Phylogenetic trees resulted from separate analyses of individual genes were shown…”

Line 376-377. Need 1-2 sentences to describe the results.

Line 406. Re-phrase. “higher stability”? Do you mean well-resolved and well-supported?

Line 411. Re-phrase. “not fully resolved”? Do you mean not well-supported? They are fully resolved on both trees.

Line 422. Awkward sentence. Sentence may read “…monophyly of the group that includes Clade I and Clade II receives….”
Experimental design: The data and analyses are adequate and competent.
Validity of the findings: Conclusions are convincing.
Additional comments: I have only a few comments and all of them are editorial.


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: CENOZOIC ARIDIZATION IN CENTRAL EURASIA SHAPED DIVERSIFICATION OF TOAD-HEADED AGAMAS (PHRYNOCEPHALUS; AGAMIDAE, REPTILIA)
Review round: 2
Reviewer: 2

Output:
Basic reporting: See my previous review
Experimental design: See my previous review
Validity of the findings: See my previous review
Additional comments: I am satisfied with author's corrections made in response to my previous notes.
The only small change that I can propose for the new version of the manuscript is the next:
The sentence "The arid belt of Central Eurasia ..." (lines 54-55) should be changed to "The eastern part of the Great Palearctic Desert Belt..." due to there is the single desert belt spanning from Atlantic coast of North Africa to north-eastern China.


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: TEA SAPONIN REDUCES THE DAMAGE OF ECTROPIS OBLIQUA TO TEA CROPS, AND EXERTS REDUCED EFFECTS ON THE SPIDERS EBRECHTELLA TRICUSPIDATA AND EVARCHA ALBARIA COMPARED TO CHEMICAL INSECTICIDES
Review round: 1
Reviewer: 1

Output:
Basic reporting: The indoor and outdoor toxicities of  tea saponin on insect pest Ectropis obliqua and two spider species, Ebrechtella tricuspidata and Evarcha albaria, were tested. The effect of  tea saponin on some enzymes in  Ectropis obliqua was also investigated.The results will help to find more eco-friendly insecticides that can be used in the tea garden.
    However, there are many spelling or even grammar mistakes in the paper. I have colored some. I do suggest the authors to find some English native speakers to help to improve the writing.
Experimental design: Generally speaking, the experiments were well designed. But the method still needs to be introduced in more detail.
Validity of the findings: The data were well analysed and the conclusions are well stated.
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: TEA SAPONIN REDUCES THE DAMAGE OF ECTROPIS OBLIQUA TO TEA CROPS, AND EXERTS REDUCED EFFECTS ON THE SPIDERS EBRECHTELLA TRICUSPIDATA AND EVARCHA ALBARIA COMPARED TO CHEMICAL INSECTICIDES
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article feet generally standards, but some literature references (given below) can be added to ameliorate discussion of the results.
some lack in introducing the research:
Abstract
the background of the article only talks about the effect of TS on Ectropis obliqua, while all the article talks about the caterpillar and two other spiders. Try to include work on spiders at the abstract level.

introduction
The author does not say why he chose these two spiders to do his study, are they predators of Ectropis?, it must be specified and prove it using references on relation between Ectropis and spiders.
Experimental design: some lacks in describing material and methods:

in Toxicity assay of insecticides to spiders
- This part to put right after the tests on the larvae of E.obliqua and before the enzymatic activity

- A dilution of 0.01 and 0.05 was made for both chemicals, explained why you used these dilutions, are these dilutions advised by the manufacturer of chemicals?.

- Say whether the spiders undergo continuous breeding or if they are simply kept up to experience. In the second case, say whether the author has verified that the individuals coming from the field are not previously treated with insecticides ...

- The number of spiders and the number of repetitions used in the test was not specified. Please give these informations in material and method
Validity of the findings: this article gives some important results, but these results must be more discussed with articles dealing with mode of action of saponins.

-	Line 245 pea aphid is not Spodoptera littoralis, and cotton leafworm caterpillars is not (Acyrthosiphon pisum). There is inversion in scientific names.
-	Discussion on the physiological effect of saponin is done without discussing one of the most documented mode of action: interaction with cholesterol, and cytotoxicity
 Try to discuss this with some references as:
http://www.iresa.tn/tjpp/tjpp9/tjpp9/4Ikbal.pdf
http://www.scialert.net/qredirect.php?doi=jbs.2007.95.101&linkid=pdf
https://www.researchgate.net/publication/6421088_Insect_growth_regulator_activity_of_Cestrum_parqui_saponins_an_interaction_with_cholesterol_metabolism
Additional comments: -	title must be changed
The author says in the title that saponins do not cause significant harm on the tested spiders. Significant habitually compared to control? in Table 2 there is spider mortality of 16.6 and 20%, but here you do not report the mortalities of control.

So to be able to say that the mortalities are not significant, it is necessary to put the values of mortality of the non treated control (even if the latter are null) since here it is an uncorrected mortality, and also it is necessary to make the comparison of the average between the control and the TS to be able to say that the mortalities are not significant.

In addition to Table 4, which relates to the garden test, there is a significant difference between control and 30% TS, so  there is an effect of saponins on spiders.
I propose to change the title, replace "non significant harm" by "reduiced effect"


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: TEA SAPONIN REDUCES THE DAMAGE OF ECTROPIS OBLIQUA TO TEA CROPS, AND EXERTS REDUCED EFFECTS ON THE SPIDERS EBRECHTELLA TRICUSPIDATA AND EVARCHA ALBARIA COMPARED TO CHEMICAL INSECTICIDES
Review round: 1
Reviewer: 3

Output:
Basic reporting: Title: Specify the TS species and the evaluated spiders.

You have to be careful in some terms and spaces when writing the text. Line 31, indoor, suggestion, laboratory. Line 41, were inhibited.

Summary: Background, does not talk about spiders and their importance in the work. Methods, does not specify the use of insecticide products against spiders and is an issue that is addressed in the results section.

Introduction: line 56: Camellia sinensis is tea saponin or is the extract of the plant which is called like that? The first paragraph can be linked to the paragraph on line 85-91 since the information is related.

Line 67: E. oblicua, attacks all types of tea crops or only some species? Be more specific.

Figures: They look with a lot of resolution. See if it is the right amount of pixels. The tables are well structured. Review writing in figure 3.

hyphotheses
It is necessary to specify why the evaluation of the enzymes is important for this work in the introduction, on the basis of which, to formulate the hypothesis again. Be clearer previously in the introduction of why use 30% TS in the field, since it is assumed that this is the dose or quantity that will have an effect on the larvae. Eliminate We hope to gain useful information to extend the application of TS, this phrase is already a perspective of the work.
Experimental design: The study gives us the idea of having more extracts or compounds of plants with insecticidal activity to avoid the use of chemical insecticides. However, it is not clear why the study of spiders, it must be more forceful in the main idea.

In some experiments in the technical standard, the analysis criteria are not defined. TS: they do not mention because they use a commercial, line 120 and not one of the tea plants of any of the bushes they mention. Larvae, specify because it was the best technique to provide ts and not formulate a diet where it is ensured that the larva consume all the concentration of TS. enzymes, they do not mention how much the units are equivalent, they leave it to the criterion of the use of the kits.

The method for the enzymatic determination is not clear, it is not specified what part of the larva were made, nor the conditions to be followed for the analysis of them, so the repetition of the experiment may be unsuccessful.

It is not clear why they decided to use Bi and Di at different concentrations, when you normally compare with the same concentration, including 30% of TS. Be clearer in these analyzes since they are the main structure of the article.

It does not make clear how the determination was made to continue the evaluation with 30% of TS. Where did the specific value come from?
Validity of the findings: The experiments are based on bibliography, but they are not explicit and therefore some results are not clear.

In Figures 1-4. The data obtained with the control show activity of the specific enzymes with water as a control. It is not explicit how this phenomenon occurs, and in their case, they do not state how good the result of the effect of adding 30% TS is. Specify the importance of the data based on the literature already reported.

The statistics in Table 3 are not clear, low, intermediate and high values share the same letter, so they belong to the same group of statistical analysis, which, it can not be possible. Review the statistics and specify the explanation in the caption or in the results section.

The conclusion agrees with what was established with the study questions and the results obtained.
Additional comments: The information generated by the authors and reflected in the article is very interesting, from the level of the generation of organic insecticides. However, it is not emphasized in providing the specific information in the methodology and in the discussion of them. The article needs to be modified in the framed sections for its probable publication.


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

Input:
Title: TEA SAPONIN REDUCES THE DAMAGE OF ECTROPIS OBLIQUA TO TEA CROPS, AND EXERTS REDUCED EFFECTS ON THE SPIDERS EBRECHTELLA TRICUSPIDATA AND EVARCHA ALBARIA COMPARED TO CHEMICAL INSECTICIDES
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have tried their best to improve the writing. However there still many gramatical mistakes. For example, it should be written as "the toxicity to" or "on" but  it was written as "in" in some places in the paper. For the insecticide name, it should be written as "the percentage of the active incgredient"+ "active ingrediant name"+"formulation name",. In the field experiment, "30% tea saponin wettable granule "was used, if I am right, however, where was this product from was not introduced. In the reference part, there are some mistakes, too.
Experimental design: Generally, the experiments were well designed. However, the counting method for the spiders was not illustrated. For enzyme activity assay, it was said that the surviving insects after insecticide treatment were used, but when were the insects were sampled?
Validity of the findings: When the authors  explained the inhibition effects of tea saponin on the carboxylesterase, they said  that helped to increase the susceptibility of the insects to that. However, that was not complete, because the underlying mechanisms related to the effects of carboxylesterase on insecticide susceptibility lie in two sides, one is to degrade the insecticides and the other is to seperate the insecticides from the hymolimph
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: TEA SAPONIN REDUCES THE DAMAGE OF ECTROPIS OBLIQUA TO TEA CROPS, AND EXERTS REDUCED EFFECTS ON THE SPIDERS EBRECHTELLA TRICUSPIDATA AND EVARCHA ALBARIA COMPARED TO CHEMICAL INSECTICIDES
Review round: 2
Reviewer: 2

Output:
Basic reporting: all corrections submitted to the author were considered
Experimental design: all corrections submitted to the author were considered
Validity of the findings: all corrections submitted to the author were considered
Additional comments: all corrections submitted to the author were considered


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: TEA SAPONIN REDUCES THE DAMAGE OF ECTROPIS OBLIQUA TO TEA CROPS, AND EXERTS REDUCED EFFECTS ON THE SPIDERS EBRECHTELLA TRICUSPIDATA AND EVARCHA ALBARIA COMPARED TO CHEMICAL INSECTICIDES
Review round: 2
Reviewer: 3

Output:
Basic reporting: Introduction.
Line 73: Add reference of the antecedent.
Line 80: Delete and before the reference of Yang et al.

Materials and methods.
Line 109: Modify the wording. Be aware that they are the larvae of the two spiders. I understand that the work is only used on adult spiders.
Lines 145 and 153: How is the percentage of mortality quantified?
Line 162: Difference of type of letter or points of the same. Make change.
Line 169: what does it mean 30% of TS (300 mg / ml)? Since it is not understood before in the text how or from where it is obtained.

Discussion.
Line 254: Mention that the results are similar, refer to other jobs reported with TS or that are similar because extracts from other plants, kill the same plague evaluated in this work? review the wording.
Line 336: Review Mansour reference is not found in the bibliography.

References.
Lines 434-436, 532-534: Differentiate the references with letter or number to locate them in the part corresponding to the article.
Line 467: The reference in the text was not found.
Experimental design: Experimental designs according to what was evaluated.
Validity of the findings: Acceptable results, conclusion according to the results and robust statistical data.
Additional comments: I know that if they corrected the article as requested. Review the details that are requested of the writing and lack of some references.


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

Input:
Title: INFLUENCE OF ALLELIC VARIATIONS IN RELATION TO NOREPINEPHRINE AND MINERALOCORTICOID RECEPTORS ON PSYCHOPATHIC TRAITS: A PILOT STUDY
Review round: 1
Reviewer: 1

Output:
Basic reporting: The present research article sought to study PPI-SF scores stratified by allelic variations in SNPs related to the NE receptor and MR.

The study seems well conducted. Nevertheless, I want to make some suggestions.
Experimental design: The study design is well defined and meaningful. Previous literature on this topic is sparse.

However, reading through the manuscript I want to make some suggestions:

1.) Introduction:
The introduction is well structured. However, I would also include some hippocampus literature when introducing the MR to the reader.

2.) Methods;
The methods are clearly explained.

3.) Results:
3a) Table 1 needs revision:
Why is table 1 showing 3 groups? This is not relevant for the main results, and I would suggest to simply make an overview of the total sample or show a table 1 stratified by the investigated allelic variations and present differences in means between the groups.
Furthermore, the first row of table 1 shows a total N = 47, which is not the case, since it  should be a total N = 57.
Moreover, the authors should clarify what the Tower of Hanoi (3, 4, 5 disk tower) variables indicate (mean number of trials?).

3b.) Figure 1a+1b and Figure 2:
The N's in Figure 1+2 are confusing.

Figure 1a-d shows N = 57.
Figure 2 only shows N = 45.

Why is the N in figure 2 smaller? Please clarify what happened to the missing subjects.

The authors should mention, that their groups have different sample sizes in figure 1a+b (N=43 vs. N =14) and figure 2 (34 vs N=11). This should be considered when choosing the statistical test and during the interpretation the results.

4.) The findings are interesting, but can these findings also be (better be) explained by other psychological measures? Did the authors control for any other behavioral measures, such as depressive behavior (BDI?), anxiety (BAI?), or other scales?
Validity of the findings: Overall, I would recommend to revise the points mentioned above.
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: INFLUENCE OF ALLELIC VARIATIONS IN RELATION TO NOREPINEPHRINE AND MINERALOCORTICOID RECEPTORS ON PSYCHOPATHIC TRAITS: A PILOT STUDY
Review round: 1
Reviewer: 2

Output:
Basic reporting: Line 49: consider clarifying what is meant by “dysfunctional amygdala”

Line 53, 54: the authors might want to consider discussing why the relationship between NE and alpha amylase is relevant in this context

Line 56-59: beta blockers do not block all the effects of NE. For clarity, it would be important to discuss why beta adrenergic receptors are important here, and the role of alpha adrenergic pathways. Also, avoid using blanket statements such as “inhibited the functioning of the amygdala.” Please clarify what is meant and which aspect of amygdala functioning is inhibited.

Line 60-61: The authors might want to contrast these findings with the role of NE in aggression (which in turn is associated with psychopathy). In general, aggression is associated with low levels of NE but high CSF NE has also been described as a predictor of violence in some studies.

Line 64: consider discussing MR in the prefrontal cortex where it is also expressed given the executive function changes in psychopathy

Line 65: It is unclear what “peripheral traits of psychopathy” really means

Line 76: The connection between childhood emotional neglect and psychopathy needs to be clarified further

Line 80: please explain how it is mitigated
Experimental design: Line 100-103: please describe how and why these 2 SNPs were selected

Line 107: why did the authors recruit at a fire department?

Line 134-146: the authors should consider what this test measures

Methods section: the PPI is a measure of psychopathy traits. Examining its results as a continuum in a population without ASPD is not validated. As such, the interpretation of how they relate to genetic variability can be faulty.
Validity of the findings: Results section: the connection between psychopathy and executive abilities is unclear. Overall, it appears that the relationship between the two measures and the genetic variability is missing.

The discussion needs to be redesigned with the above described concerns addressed. Otherwise, the conclusions present significant limitations.
Additional comments: General comments:
-	In general, it is preferable to use DSM5 terminology. While there are certainly phenomenologic differences between psychopathy and sociopathy, I recommend using the overarching umbrella term Antisocial Personality disorder. This would still allow for further breakdown into psychopathy traits (which carry a lot of historical/social/political/legal weight)

Specific comments:
Line 45: consider adding developmental to the causes of psychopathy: “genetic, environmental [and developmental] factors”


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

Input:
Title: INFLUENCE OF ALLELIC VARIATIONS IN RELATION TO NOREPINEPHRINE AND MINERALOCORTICOID RECEPTORS ON PSYCHOPATHIC TRAITS: A PILOT STUDY
Review round: 1
Reviewer: 3

Output:
Basic reporting: There are some grammatical errors in the manuscript but overall the language is sound.

The background evidence presented is of decent quality but it is not well interpreted, as I don not understand what "peripheral traits" in psychopathy are and they are not explained.

Also, the author does not explain what the connection between resilience and psychopathy is. Is it that psychopaths are more or less resilient?

The author speaks of "successful psychopaths" and "unsuccessful psychopaths" being different but does not explain what that means or how it is really relevant in this study.

I reviewed the article that they cite on The Tower of Hanoi and psychopathic tendencies (DOI: 10.1080/09084282.2010.52338). The article looks at Psychopathic traits and compares the performance on the computerized version vs. the manual version. They conclude that low/moderate psychopathy scorers performed poorly on the computerized Tower of Hanoi while high psychopathy scorers performed better on the computerized version in comparison. The conclusion was that high scores on computerized Tower of Hanoi tests should be interpreted with some caution as a result, and was not really related to the psychopathy traits the way the authors of this paper seem to imply.
Experimental design: The data surrounding NE and MR and psychopathy is nebulous at best. It was difficult to understand what the hypothesis they were testing was.
Beta Blockers do not "block" NE- they decrease response to it by competing for the receptors. This is an important distinction because some beta blockers have partial agonist activity which modulates response to NE/E and also changes the cellular response to the hormones.
As for MR receptors, it's true they're expressed in the amygdala, but what about the cortex and the prefrontal cortex? If they're commenting on executive functioning and correlating it psychopathy using the Tower of Hanoi test, then it would make sense to discuss the role of the prefrontal cortex/cortex in executive functioning and planning.
The SNPs that were chosen: why those in particular? One of them is the transporter for NE and one of them is just part of the MR gene. I don't really understand why those are relevant.
As for the use of the PPI-SF, for the most part that methodology was sound, as this scale was normed on college students. I do not particularly understand why they chose to use firefighters, however. Was there a particular type of trait in firefighters that they were looking for?
Validity of the findings: Although I am unsure of why they chose these SNPs, the processing of the samples is sound. The use of the PPI-SF is proper as this test is only normed on normal subjects and not psychopaths or jail populations.
The Tower of Hanoi test was administered properly.
The issue I have is there are a lot of jumps in logic that are not well explained by the author. He makes leaps in his conclusions and manipulates the data in a questionable manner in order to get some sort of correlation between the SNPs, the results on the PPI-SF, and the Tower of Hanoi test.
The data itself, in its raw form, may someday prove valuable, the same way genetic mapping with schizophrenics, provides databases of material that may someday unlock the mystery of the illness.
That said I do not really understand the author's conclusions which are based on arbitrary alleles (or they are not explained well enough so they seem arbitrarily chosen to the reader of the article), performance measures on the Tower of Hanoi test that measure executive functioning and ability to plan, and the PPI-SF which measures psychopathic traits in a normal population.
Coupled with a small sample size, the conclusions require a leap of faith to accept and I feel that they assume causation when they barely meet the standard of correlation.
Additional comments: The data is valuable because all data collected, especially when you're doing genetic work, can be valuable in the future. The interpretation of the results obtained is questionable at best, and is stretching the conclusions further than I think they can truly go.


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

Input:
Title: INFLUENCE OF ALLELIC VARIATIONS IN RELATION TO NOREPINEPHRINE AND MINERALOCORTICOID RECEPTORS ON PSYCHOPATHIC TRAITS: A PILOT STUDY
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have edited their article based on the suggestions I have made. They improved their manuscript, and clarified the paragraphs I have pointed out in my first review. For a more detailed review, please read my prior review.

Hence, I support to publish this article.
Experimental design: see above / prior review.
Validity of the findings: see above / prior review.
Additional comments: see above / prior review.


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

Input:
Title: INFLUENCE OF ALLELIC VARIATIONS IN RELATION TO NOREPINEPHRINE AND MINERALOCORTICOID RECEPTORS ON PSYCHOPATHIC TRAITS: A PILOT STUDY
Review round: 2
Reviewer: 2

Output:
Basic reporting: I want to commend the author on cleaning up the language used. The manuscript flows better and reads much clearer.
The references are also properly used to explain the hypothesis and the background sets the stage in a much more effective manner.
The figures are simplified nicely and more relevant.
The hypotheses are clearly stated and the results are much more relevantly presented.
Experimental design: The research question is simplified and the experimental design used remains sound.
Validity of the findings: The results as stated currently are much more valid and useful to the reader. I am impressed with the author taking reviewers' feedback into consideration and the modifications have made the article significantly better.
Additional comments: Revisions are well done. Manuscript much clearer.


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

Input:
Title: THE EFFECT OF TIDES ON NEARSHORE ENVIRONMENTAL DNA
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment
Additional comments: General comments
The need for the research is clearly stated, the study design is clear, the analyses are rigorous and easy to follow, and the conclusions do not extrapolate beyond the results.  Taken in total, this is an outstanding contribution that I have very little to be critical of.  I strongly advocate for the manuscript’s publication in PeerJ.  I have only two discussion points I would like the authors to consider.

At each sampling location (Lilliwaup, Potlatch, and Twanoh) three samples were collected approximately 10 m apart. My experience with intertidal areas, along with my expectation that there is considerable water mixing at the nearshore would lead me to a priori expect that water samples taken this close together would necessarily be very similar, both on the incoming tide and outgoing tide.  Finding consistency among samples at a site could be a function simply of a well-mixed system and not necessary a reflection of local species.  Alternatively, do deep water species (likely not in the intertidal area) showing up in the samples?  I suggest more scrutiny of the species detected and their likely location in the system is justified to provide stronger evidence for the conclusions.  I fully agree that between the three locations there are differences in species composition, and the authors have solid ground to talk about localized scale of inferences.

Additionally, Shogren et al. (2017) talked about retention of DNA.  What role would retention of eDNA trapped in tidepools, on macrophytes, trapped in the sand and then re-suspended play in the detection signal?

Shogren, A.J., Tank, J.L., Andruszkiewicz, E., Olds, B., Mahon, A.R., Jerde, C.L. and Bolster, D., 2017. Controls on eDNA movement in streams: Transport, retention, and resuspension. Scientific Reports, 7(1), p.5065.

I don’t know the answer to this, but given the potential wave action influence going could the low tide shift to hi tide purely be a legacy effect of DNA being “trapped?”


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 EFFECT OF TIDES ON NEARSHORE ENVIRONMENTAL DNA
Review round: 1
Reviewer: 2

Output:
Basic reporting: This manuscript is clearly written and the literature citations are very thorough. The article structure, figures, and tables are appropriate and clear, and the raw data will be shared upon publication. The results are consistent with the hypothesis the nearshore eDNA communities change in unpredictable ways.
Experimental design: This is an interesting ecological/environmental study that is appropriate for PeerJ. The research question ("Do eDNA communities change with tides in nearshore coastal environments") is well defined throughout the manuscript and fills in a significant gap in our knowledge of eDNA dynamics. The experimental design was appropriate and, although a few more sites would have been ideal (3 sites included in the study), sufficient to answer the main question. The eDNA collection, amplification, sequencing, bioinformatics, and statistical protocols all followed best practices in the field.

My only methodological concern is with the treatment of negative filter controls. The statement of Page 3, Line 91 "... but did not sequence them [negative controls] due to the practical and theoretical issues associated with library preparation in samples without any discernable amplicon." needs a citation. I know of many studies that do sequence these samples, even if no PCR band is present. Also, given the high possibility of cross-contamination at the sample collection or filtering stages of this study, skipping the sequencing of the negative filter controls is an issue. Also, please note somewhere that using the Ostrich samples to gauge cross-contamination won't detect contamination that occurred during sample collection or filtering stages, just lab contamination.
Validity of the findings: no comment
Additional comments: Overall this was a well-written and rigorous study that provides new insight into the "ecology" of nearshore eDNA communities. I have only two few minor comments/suggestions in addition to the negative filter controls concern mentioned previously.

1) Given that PCR bias is inherent in any metabarcoding study (which the authors do a nice job of explaining), shouldn't a presence/absence dissimilarity metric (e.g. Jaccard) be used instead of the abundance-based Bray-Curtis? As the authors say (Page 10, Line 255), the read count abundances don't reflect the true abundances of the organisms.

2) Page 11, Line 277: change "provide" to "provides"


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 EFFECT OF TIDES ON NEARSHORE ENVIRONMENTAL DNA
Review round: 1
Reviewer: 3

Output:
Basic reporting: This manuscript uses molecular surveys to compare the biodiversity of eukaryotes living in nearby coastal sites, with the emphasis to see if communities are changing during different times of the tidal cycle. The authors identify two different communities, that are characteristic of different sites. The paper is well written and well presented, but I have a major concern relating with the focus of the study.

My main concern is the poor definition and understanding of what environmental DNA (eDNA). Reading the introduction, the authors seem to imply mostly dissolved or extracellular DNA, that leaves remnants of living cells. The comes from the use of references mostly from metazoans, and specially from the first sentence in the introduction: "organisms leave genetic traces". But then, the data derives from planktonic eukaryotes that live in 1 liter of water and are larger than 0.45 µm. So, basically the thousands of planktonic protists in this water mass (and the few animals that by chance may be collected in this liter of water). So, this is essentially a study on planktonic protists. And on top of that, there is the signal of dissolved DNA released as genetic traces from benthic fauna and flora. The first and needed analysis here would be to separate, as much as possible and based on the taxonomic identification of the sequences, the signal from planktonic microbes and from benthic organisms.

This is very important for the conclusions, as the molecular signal has two components, one that is static and depends on the benthic organisms, and another that is dynamic and depends on the microbes that the water mass is carrying (always they come and they leave the site).

Other comments:

Line 169. "etc" in a heading does not sound right

Line 201. The range "0.26 to 1" is not right

Line 209. Instead of "individual environmental changes" what seems to happen in this individual point is "a water mass replacement", bringing the community that lives in the other site. The same argument in line 238

Line 231. Typo in Associated

Line 262-264. Again this sentence represents the main problem of the manuscript: what is the habitat here? Studying planktonic eukaryotes, the habitat is moving with the tides, so the habitat is itself "exogenous". This seems to arrive at the end of the manuscript, as a surprise (lines 296-297), but in fact is a well known fact that collecting planktonic microbes on filters is the standard way to study their biodiversity.å

Fig 6,  bottom. I suggest here to add an extra category with the signal of the "other groups". This will bring a more fair comparison of the different families
Experimental design: The design is fine and appropriate for the actual study
Validity of the findings: As said before, the main problem here is to differentiate between the signal coming from planktonic microbes and benthic organisms.
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 EFFECT OF TIDES ON NEARSHORE ENVIRONMENTAL DNA
Review round: 2
Reviewer: 1

Output:
Basic reporting: xx
Experimental design: xx
Validity of the findings: xx
Additional comments: My main concern of this paper, an important one, was that the authors neglected what I think could be the most important source of their molecular signal. To me, the molecular analysis of what is retained after filtering 1 liter of seawater through a 0.45 µm filter targets mostly microbes that lived suspended in seawater (millions of cells). And this has strong implications to the results shown here. Certainly, there can be signal from other sources (dissolved or detrital DNA retained in the filter, small animals that lived in this particular liter of water, or fragments of animals and macroalgae). But I still think that this "organismal" DNA is more important than the "genetic traces" of benthic organisms. And at any rate, the relative importance of both elements needs to be stated.

In their response, the authors seem to be aware of the existence of planktonic microbes and make a long answer to this general comment, but then when I look at the manuscript, the paper looks essentially the same. So, this essential fact has not been mentioned at the introduction and is very superficially treated in the general conclusions.

Just in the abstract there are good examples of how my main concern has not been addressed:
"Organisms of all kinds leave behind genetic information in their environments"
Yes, there is the genetic signal left by organisms but, on top of that and likely more importantly, there is the signal of the organisms (in this case microbes) living in the actual sample taken.
"Our findings suggest that nearshore eDNA tends to be endogenous to the site and water mass sampled, rather than changing with each tidal cycle"
Given that the sample analyzed has two components (and this should be explicitly mentioned, treated, presented, and discussed), I disagree with this sentence. There is a component that lives in the water, so it comes and goes with the tides. If the site is the "geographic coordinate", this component is exogenous by definition. And then there is the component that derives from the benthic organisms, which are less mobile and therefore essentially endogenous.


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: LARGE-SCALE ASSESSMENT OF COMMENSALISTIC–MUTUALISTIC ASSOCIATIONS BETWEEN AFRICAN BIRDS AND HERBIVOROUS MAMMALS USING INTERNET PHOTOS
Review round: 1
Reviewer: 1

Output:
Basic reporting: There are a few places where sentences didn't make sense and minor rewording is needed, but in general, the paper was clear, well written, and structured fine.
Experimental design: The authors use a novel source of data to examine relationships between African birds and mammals. In general, the aims of the study were clear and the methods adequately described.
Validity of the findings: Mostly fine, although I have a couple of suggestions.
Additional comments: This is an interesting use of citizen science data to investigate the apparent mutualistic relationships between birds and mammals in sub-Saharan Africa. Their use of data has various limitations, most of which the authors seem aware of and deal with appropriately. The one variable I would recommend they delete from the analyses is elevation, unless they can generate some a priori hypothesis for why it might be important. I also still don’t understand what “nestedness” means, exactly, in the context of their analyses. Since this plays a fairly important role in their discussion, I would recommend they try to explain it better for those of us who are not familiar with this concept. In general, however, I think the authors did an interesting job of using photographs to infer and in some cases even test prior relationships between African birds and mammals.

Specific comments:

Lines 28-32. I don’t think it’s necessary to devote space telling readers that the savanna is not uniform.

Lines 70-81. Most of this seems peripheral (at best) to the paper. Delete or reduce.

Line 76. Not quite a sentence…reword (“This may cause that…”)

Lines 91, 98, 168. Avoid “e.g.”s and “see also”s; all citations are but representative of those that could be cited.

Line 99. Avoid “the first”; maybe it is, maybe it isn’t, but it’s asking for it in a way that’s unnecessary.

Lines197-198. The suggests that when an exact location was not specified, the elevation of whatever the center of the species in that country was used. This seems way too likely to introduce potential bias. I would exclude such cases when it comes to elevation and habitat. Actually, it’s unclear to me why elevation was analyzed at all; what is the rationale for including it as an explanatory variable? Given that it’s not significant anyway, I’d suggest throwing it out.

Lines 208-228. I understand the webs, but I don’t understand how this particular one could be nested, or what, exactly, a “nested web” means or would look like in this case. Please clarify.

Lines 248, 257. Round r value to 2 decimal places.

Line 253. “avoid” or “circumvent” rather than “eradicate”.

Lines 342-345; 353-357. Round off these and other values to 2 decimal places, please.

Lines 341-347. Again, I don’t really understand what “nestedness” means in this example.

Line 352. Please clarify what “a negative relationship with habitat openness” means.

Lines 374-375. Unclear what “higher bird mass” refers to, exactly.

Lines 411-412. Reword (“In result…”); also delete second MacArthur and Wilson references.

Lines 447-457. This helps but it’s still not clear to me what nestedness would look like in this situation.

Lines 475-480. This strikes me as far less likely than that sampling by photographers is incomplete (the author’s alternative explanation). I’d delete. It's speculation at best, but speculation that is too important to throw out without better evidence.


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: LARGE-SCALE ASSESSMENT OF COMMENSALISTIC–MUTUALISTIC ASSOCIATIONS BETWEEN AFRICAN BIRDS AND HERBIVOROUS MAMMALS USING INTERNET PHOTOS
Review round: 1
Reviewer: 2

Output:
Basic reporting: 1. Language
The English is generally fine, but could still be improved. At a number of places, the article is missing. Throughout the text, weight should be replaced by body mass (currently there is a mix of both terms).

2. Background/context and references
While the manuscript makes a few cross-references to work performed outside Africa, it ignores important recent literatur.
The recent book by Goodale, Beauchamp & Ruxton (2017; Mixed-species animal groups: behavior, community ecology and conservation) provides a broad and comprehensive background to interspecific mutualistic and commensalistic interacts. Consulting this work will help to draft a more focussed background and sharpen the research question (see below).
Heymann & Hsia (2015; Biol Rev) reviewed the interactions of primates and other animals. Although they did not perform sophisticated statistical analyses, they also examined the influence of various factors (e.g., body size, group size) and reached some conclusions that might be relevant for the discussion.

3. Article structure etc.
The manuscript meets the expectations with regard to the structure and figures. Raw data are provided as supplements.
Table 1 needs to be improved. The two separate sets of results (for full data set and for restricted data set) are not visually clearly separated. It took me a while to match the information in the text with the content of the table. I suggest to use additional headers in the table, one over the columns referring to the full data set, and another over the columns referring to the restricted data set

4. Self-contained ...
This is a major weakness of the manuscript. Hypotheses and predictions are not explicitly stated. This strongly diminishes the value of the manuscript, as it makes it more difficult to understand the results.
Experimental design: 1. Aims and Scopes
The manuscript fits with the aims and scopes of the journal.

2. Research question ...
Examining patterns of interspecific mutualistic and commensalistic interaction is a rapidly expanding field in ecology, with broad implications for understanding e.g. ecosystem functioning, adaptations and conservation. With regard to interactions between mammals and birds, there is a large amount of mainly anecdotal information, but very few reviews and quantitative analyses. Therefore, the topic of the manuscript is of considerable interest and could potentially contribute to filling gaps in our knowledge.
However, in its current form the manuscript shows a number of problems, identified in the following:
a. Mutualism and commensalism are mixed up. Certainly, there is no strict limit (as is most often the case in biology) between categories created by scientists. For some interactions between organisms, e.g. ant-plant interactions, the interaction type may even range from mutualism to parasitism. Nevertheless, it would be useful to distinguish mutualistic and commensalistic interactions and to categorize the species combinations accordingly. Obviously, the "cleaning" interaction between oxpeckers and mammals is clearly different (both parties generally benefit) from the "sitting" interaction between e.g. egrets and mammals (only the birds benefit). Mixing up mutualistic and commensalistic interactions is as problematic as if one would mix-up seed dispersal and pollination in animal-plant network analyses.
b. As I understood the manuscript, analyses are restricted to those interactions where the birds sit (either for sitting or for cleaning) on the mammals, but excludes birds flying around mammals. Altough the criterion to restrict the analyses to photos showing birds sitting on mammals has the advantage of using a simple criterion, it probably eliminates many (commensalistic) interactions of birds that associate with mammals without regularly sitting on them. I think that this needs to be more strongly considered in the conclusions.
c. The research question is not very well defined. It took me two readings of the Introduction to (hopefully) understand what the authors actually intended to study. This problem is aggravated by the fact that the authors unnecessarily introduce reasons for their analyses that are honourable - namely conservation of savannahs and of the interactions therein -, but that are scientifically not really needed to justify the study. Furthermore, the justification in terms of conservation is partially not correct: when the authors state (l. 71) that "Savannahs are one of the most threatened world", this is only correct for temperate but not for tropical savannahs (Conservation Risk Index 10.1 for the former, 2.0 for the latter; see Fig. 1 in Hoekstra et al).

3. Rigorous investigation ... & Methods ...
a. As mentioned above, the lack of distinction between mutualism and commensalism is a basic problem.
b. Otherwise, the procedures for selecting the photographs from the internet are well described and allows for potential replication.
c. While the authors include geographic information, they do not correct for the potential effect of spatial autocorrelation. Many photos are likely to come from the same sites frequently visited by tourists and scientists. This may inflate numbers for certain species combinations. The lack of controlling for this potential bias is in marked contrast to the otherwise sophisticated statistical analyses, including phylogenetic corrections.
d. It did no become clear to me what your sample unit is. As I understood, it is one interaction, i.e. one or more birds sitting on a mammal. But it is not clear whether photos showing several mammals, each with one or several birds from the same species, are scored as one or as several interactions (the latter violating statistical independency).
Validity of the findings: Given the problems identified above, it is difficult to evaluate the validity of the findings.

As with the justification of the study, there is also some overstament with regard to conservation in the Discussion. As long as it is not known which proportion of resources birds derive from the interaction with mammals (except for the obligatorily interacting oxpeckers), the conservation implications of the drop-out of interaction parners cannot be evaluated, in contrast to e.g. seed-dispersal mutualism where the effects of drop-out have already been robustly demonstrated.
Additional comments: Despite my criticism stated above, I like the approach taken by the authors. Commensalistic interactions may play larger roles in ecology than is generally appreciated, but we are far from understanding their impact. Therefore, analyses that tackle patterns of commensalistic interactions are highly welcome. I think there is a large potential for making an important contribution to the understanding of interspecific interactions between birds and mammals once the problems addressed above have been solved.


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 IDENTIFICATION OF GALECTIN-11 AND 14 LIGANDS FROM HAEMONCHUS CONTORTUS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The work was well developed and is clearly written. The authors identified glycoproteins of Haemonchus contortus ligants to galectins of the host and evaluate the putative importance of these proteins to development of vacccines against the parasite.

Line 43: There is not any previous information about "these glyocoproteins".
I think that it is necessary to include information about glyocoproteins before this sentence.

Line 47: please, include references.
Line 48 : add the expression "the expression of" between "upregulate" and "two"

Line 214: add an space in "andtranslation"
Experimental design: Line 168: Was it used a ovine database to identify host protein contamination?  I think it is an important control for a better analysis.
Validity of the findings: Line 217: Are actin myosin and collagen from host or from parasite?
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 IDENTIFICATION OF GALECTIN-11 AND 14 LIGANDS FROM HAEMONCHUS CONTORTUS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Manuscript is generally well written, although there are grammatical corrections needed and English should be reviewed to improve the paper. There are occasional misspellings and grammatical errors throughout the paper. Manuscript does not require expert English editing, but a thorough reading of the final draft is necessary. I have added some comments and suggestions to authors in "General comments for the author".
Experimental design: Experiments  were well designed and conducted properly.
Validity of the findings: The study describes L4 and adult H. contortus-derived proteins interacting with host galectins using a pull-down assay followed by LC-MS/MS.

This manuscript contains very useful information for the field and findings described by authors might have implications for the design of new and efficient anti-H. contortus vaccines.

I appreciate authors already had deposited raw LC-MS/MS data on a public repository.

The main weakness is that authors failed to discuss some proteins (such as peptidase S28, alpha beta hydrolize) which were identified in high abundance.

I have added some comments and suggestions to authors in "General comments for the author".
Additional comments: The manuscript "Proteomic identification of galectin-11 and 14 ligands from Haemonchus contortus” uses pull-down assay followed by spectrometry-based proteomics approach to identify H. contortus proteins that interact with host galectin-11 and galectin-14. The experimental design is well conducted and manuscript is generally well written, although there are grammatical corrections needed and English should be reviewed to improve paper. Some points need to be corrected/clarified before I can recommend it for publication. These are my suggestions:

Major comments:

Material and Methods:
Line 132-133: how much total protein was diluted and applied on column?

Results and Discussion
Composition of LGALS-11 and LGAL-14 ligands:
Line 223-226: in addition to glycan-independent interaction, authors should discuss other types of glycosylation already describe in other organism that are not predicted by tools used in this study.
Please see: Schachter, H. Protein glycosylation lessons from Caenorhabditis elegans. Current Opinion in Structural Biology, 14(5), 607-616, 2004

Protease and phosphatase ligands
Line 256-259: missing discussion about the role(s) of metalloproteases into parasite-host relationship.
Why did not authors discuss in depth the identification and the putative role(s) of “peptidase S28” and “alpha beta hydrolase fold 1”?
According to peptide spectrum matches on Table 1, “peptidase S28” and “alpha beta hydrolase fold 1” appear as the most abundant proteins identified in this study.
Similarly, would suggest to analyze homology/similarity among entries identified in this study and classified as peptidase S28 (W6NE18, W6NFT9, W6NG90).

Tables and Figures
Table 1: I would like to suggest authors to include NSAF values for identified proteins.
I would like to suggest changing “Host-parasite interaction” classification, since all proteins identified could be classified in this class (same for Figure 4).

Table 2 should be removed or presented as Supplemental information, since information contained (presence in adults) is also presented at Table 1 (Groups 2 and 4). Signal peptide and glycosylation predictions should be incorporated at Table 1. I would like to suggest authors to include the number of putative N- and/or O-glycosylation sites for each entry. Description of molecular mass for each protein at Table 1 also would be useful to analyze this information along with  electrophoretic profile presented in Figure 2.

Figure 1: Authors did a great job on this picture; however its content (pull down concept) is very basic. I would like to suggest to remove or include as Supplemental information.
Figure 1 legend: “L4 larvae” instead “larval”.
“…Mascot (Perkins et al., 1999) and searched against NCBI protein database”. In Material and Methods section authors described Swiss-Prot database was used.
Figure 2. I would like suggest to authors rephrase title.
Also, I would like to suggest authors to include SDS-PAGE (and results of identified proteins) from control resin (no galectin bound Sepharose). These could be presented as Supplemental information.
Figure 5. Relabel “14_Adult” and “11_Adult”

Minor comments:
Title: “galectin-11” instead “Galectin-11”.

Introduction
Line 46: “mediates”.
Line 47: “self and non-self glycans”.
Line 48: missing a bracket after “LGALS-14”.
Line 49: if possible, please describe species names for Ostertagia and Cooperia.
Line 58-59: missing reference for this sentence.
Line 66: would suggest to replace second “LGALS-11” by a pronoun.

Material and Methods:
Line 84: “normal saline” instead “biological saline” (please review through manuscript).
Line 87: please describe which fungicide was used.
Line 114: I guess “SDS-PAGE” was left by mistake.
Line 119: “Sepharose” (please review through manuscript)
Line 126: Does not blocking buffer contain ethanolamine/glycine or another molecule to block reactive groups on resin?
Line 127: is not clear if both Tris-HCl and sodium acetate buffers contain NaCl.
General for buffer description: please standardize description (put in order molarity, compound, pH, etc...spaces after concentration, etc… try to use IUPAC recommendations).
Line 137: “galactose”
Line 144: “Mass spectrometry”
Line 161: “data-dependent acquisition”.
Line 167-170: Please rephrase this sentence.
Line 172: “were included”.
Line 174: “peptide”
Line 180: please remove “scores” or replace by "values.
Line 182: remove quotation mark after “interactome”.
Line 189: “signal”

Results and Discussion
Line 194: “Identification of proteins of H. contortus that interacting with LGALS-11 and LGALS-14” does not sound good. I would suggest to replace by “Identification of proteins from H. contortus that interact with LGALS-11 and LGALS-14” or “Identification of proteins from H. contortus interacting with LGALS-11 and LGALS-14”.
Line 195 and 196: Please rephrase this sentence.
Line 201: “…were eluted with elution buffer-containing galactose”.
Line 202: “a control”.
Line 214: “and translation”.
Line 243-248: spell out protein names using lowercase letter (please review manuscript).
Did you identified a von Willebrand factor-like protein or a protein containing a von Willebrand factor-like domain?
Line 250: “were identified in adults” instead “in adults were identified”.
Line 251: “omic” (missing a quotation mark).
Line 266: “The von Willebrand”.
Line 279: “identified interacting with host galectins”.
Line 286: reference (Yatsuda et al., 2003) is italicized.

Conclusion
Line 309: “antihelminthic”.
Table 1: “mass spectrometry” instead “mass spectroscopy”.


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 IDENTIFICATION OF GALECTIN-11 AND 14 LIGANDS FROM HAEMONCHUS CONTORTUS
Review round: 2
Reviewer: 1

Output:
Basic reporting: I have read the revised manuscript and the authors have addressed my comments satisfactorily. I now recommend the manuscript for publication.
Experimental design: I have read the revised manuscript and the authors have addressed my comments satisfactorily. I now recommend the manuscript for publication.
Validity of the findings: I have read the revised manuscript and the authors have addressed my comments satisfactorily. I now recommend the manuscript for publication.
Additional comments: I have read the revised manuscript and the authors have addressed my comments satisfactorily. I now recommend the manuscript for publication.


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

Input:
Title: PROTEOMIC IDENTIFICATION OF GALECTIN-11 AND 14 LIGANDS FROM HAEMONCHUS CONTORTUS
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: Authors addressed all suggestions made by this reviewer. I recommend article should be accepted for publication.


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

Input:
Title: PHYLOGEOGRAPHIC STRUCTURE IN THREE NORTH AMERICAN TENT CATERPILLAR SPECIES (LEPIDOPTERA: LASIOCAMPIDAE): MALACOSOMA AMERICANA, M. CALIFORNICA, AND M. DISSTRIA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is well written, with interesting results and discussion. Patterns are well illustrated and sufficient data is available to the reader.

However, there are some important issues concerning the lack of references in some statements (e.g., lines 49-50 and 88-89) and lack of background about the genus (e.g., number of valid species and distribution).
Experimental design: The most serious question that should be considered to enhance the quality of this manuscript is in the structure and coherence between objectives and methods. The objective of the manuscript (lines 98-100) is to assess the genetic structure of three species of Malacosoma and describe its phylogeographic patterns. However, some phylogenetic analyses are described, not just in methods section, but in results as well, although the reasons for such analyses are not clear in the text. After reading the manuscript, it is possible to understand that some previous phylogenetic analyses were necessary to verify the monophyletic groups the authors could work with. Then, some groups were selected, its genetic structure were described and, finally, phylogeographic patterns were discussed. I suggest that a clearer description of this methodological process could be made in methods section.

Despite of that, the patterns found for these three species of Malacosoma contribute greatly to the understanding of the genetic structure of North American species. Considering the lack of studies with insects and other invertebrates, the authors provided an important contribution to the field.
Validity of the findings: Results are well discussed and well illustrated. Although I am not familiar to genetic analyses, it seems that tables provide sufficient information to understand the description of results and discussion.
Additional comments: I made a few notes about the validity of some terms you used. Maybe you should consider reviewing them. Comments about the lack of clarity in methodology and objectives are more important to consider, in my opinion. They are not necessarily wrong, but confuse, which diminishes the quality of your work. Comments were made intending to enhance your manuscript.