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: INDICATORS FOR THE USE OF ROBOTIC LABS IN BASIC BIOMEDICAL RESEARCH: A LITERATURE ANALYSIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: In general, the manuscript is clearly written. There are some typos and small grammatical issues, which should not be difficult to address. I noted the following:
- "methodbut" -> "method but"
- "an robotic" -> "a robotic"
- "methodswithin" -> "methods within"
- "methodsin" -> "methods in"
- "methodscan" -> "methods can"
- "methodsthat" -> "methods that"
- "Finally, While" -> "while"
- "This large overlap could have to do with what the skewed distribution of recognized ..": "what" seems ungrammatical.

Some sentences are unclear or confusing, and I suggest the authors clarify them. These are as follows:
- The authors state that "this ability to have a much more detailed computational view is critical for reproducibility as narrative descriptions of methods are known to be inadequate for this task". I would think the robotic labs would have to start with the narrative description of experiments for replication. How does one go from this narrative description to computational view?
- The authors state that "Of the potential 1035 methods only 151 were recognized". Is 1035 the number of relevant MeSH terms? Earlier in the manuscript, they state there are 1036 relevant MeSH terms.
- " With the exception of cell culture, the other methods in Table 1 are also comprised of highly automatable tasks."  I thought being included in Table 1 meant  the method could be fully automated. What's the specific difficulty with cell cultures? Explain.
" 26 of these methods are in fact supported by one of these cloud labs, exposing some leakiness  in our procedure." The example given is Real-Time PCR. This seems to be a term in MeSH since 2012. Either give a more accurate example or explain the discrepancy.

There are a few figures and tables and their content is adequate. I think Figure 2 can be more effectively presented as a table, and percentages can be added. I think Figure 1 is useful, and something similar for method selection/categorization and for article/method matching would be helpful to guide the reader and tighten up Methods/Results. Currently, these numbers can be hard to follow as narrative text. The authors commendably provide the data and the code for their experiments.

Since method identification (a named entity recognition task) is core to the study, I think it would be useful to provide some background for research in this area. Currently, only towards the end of the Discussion section, this particular task is mentioned and very briefly. A more detailed discussion early in the paper would be more informative and situate this study better.
Experimental design: The notion of automatically reproducing basic research with robots is an intriguing idea that is being increasingly recognized and an investigation of how much of current research can be automated in this manner is timely and meaningful. The authors do a good job of explaining the research goals and providing the context for them.

In general, the methods are described sufficiently and since the data and the code are provided, the methods can be assumed to be replicable.

My main issue with the study is that the method identification approach does not seem powerful enough to make claims about the use of robotic methods. The authors admit this to some extent, stating that their results are likely to underestimate the use of such methods; however, I believe they could have done more with existing, off-the-shelf tools. Much information seems to be lost in mapping steps and also in method identification. I think some expert feedback or use of additional resources would be appropriate.

For example, 71 of 107 methods identified are identified in MeSH (which is a good starting point), the rest (36) seems like a significant proportion to just ignore.Why not try to use other vocabularies/ontologies for these 36 or just generate term lists, since the annotator basically performs simple string matching?  For example, OBI (ontology of biomedical investigations) comes to mind as a good candidate. Since the paper is mainly interested in assessing the coverage (and not in only automatic method identification), such interventions would be justified.Some further discussion of these 36 methods and how 71 methods identified in MeSH were mapped to 59 concepts would also be helpful (am I right to assume some methods map to the same MeSH concept?).

It is also not clear to me whether the authors tried using MeSH identifiers used for indexing articles in PubMed. I would think this would be the easiest way of answering their core question. Checking a few of the articles they considered, I can see that indexing terms for these articles include some method names. Since these indexing terms are assigned by human indexers, it can be considered a gold standard and would potentially alleviate the coverage issues noted for the annotation method the authors used. Do the authors find that these methods are not consistently or fully indexed? If the authors have not considered this, I would strongly suggest that they do. If they did, some explanation is needed regarding why they chose not to report it.

There are existing, broad-coverage biomedical named entity recognition methods such as MetaMap (Aronson and Lang, 2010). Did the authors consider using them, instead of coming up with their own lexicon-based method? They state  (in the Discussion section) that state-of-the-art in process/task detection is low (0.44 F1), but they do not provide the performance for their own method, making it difficult to assess whether the analysis can be strengthened by such off-the-shelf NER tools. Since MetaMap can be easily tailored to run against MeSH specifically, I believe it can strengthen their approach and findings without too much additional effort.
Validity of the findings: Due to the issues I discussed above, I believe the findings are suggestive rather than conclusive. The authors highlight the difficulties in using automated methods for their task in the Discussion section. I think some of suggestions (using MeSH indexing terms, MetaMap, etc.) can be considered to address some of these challenges (in particular, points 1 and 2 on lines 189-191).  However, I believe this paper is still a step in the right direction for understanding the feasibility of such approaches to reproducibility.

As a side note, I think it would still be useful (with the limitations of the approach in mind) to know how many articles (of 1011) were found to contain only robotic methods. This is never clearly 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: INDICATORS FOR THE USE OF ROBOTIC LABS IN BASIC BIOMEDICAL RESEARCH: A LITERATURE ANALYSIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The basic reporting standards have been met.
Experimental design: I see no issues with the experimental design.
Validity of the findings: Overall:
This paper nicely describes the problem of scientific reproducibility and how this could be better addressed by automating basic lab methods using robotics, where applicable. The authors demonstrate that in the corpus of papers analyzed, the majority of methods used in the experiments were assays that could be performed by robotic labs. The conclusions are supported by the analysis.

One thing that I think is missing from the discussion is how this work can impact the future of biomedical research. More specifically, now that we know that the majority of research could be performed by robotics, what are some potential ways we could implement this? A discussion of the potential issues would be nice to include, such as the issue of the expense of running robotic machines, ie not every lab could afford to purchase an automated robotic PCR machine, for example. However, this could be potentially addressed with increased collaborations with labs that already own these tools, and have optimized the protocols. This paper could also be used to promote funding agencies to support automated protocols using robotics, to further ensure scientific reproducibility.
Additional comments: Minor edits:
Abstract - first line
Should it be Robotic labs (lowercase labs)

Lines 11-12
I suggest writing 'could be applicable' in "In this article, we investigate whether these labs are applicable in current experimental practice."

Introduction- Lines 35-36
In this sentence: "These are labs in which the entire
36 experimental process is performed by robots and available remotely in the cloud (Bates et al., 2016)", what is available remotely in the cloud? The data?

Lines 54-56
State the questions as 1a and 1b, otherwise it looks like you are asking two questions.

Discussion Lines 159-161
"Our annotation procedure does not attempt to generalize: the MeSH ID a method is labeled with is exactly what is returned in a search for the method without traversing the hierarchy of the method tree."
Please reread this sentence, there seem to be some typos here.

Line 166
You are asking only one question, in two parts, so I suggest rephrasing to "In terms of the second part of the question..."

Line 174
Missing a space in methodswithin

Line 175
Missing a space in methodscan

Line 191:
Missing right parenthesis

Line 203
Missing a space in methodsthat

Line 205
"While" should be lowercase

--
Did you find any missing synonyms in MeSH? If so, did you make requests to MeSH for these new synonyms?

--
This link does not resolve, it needs to be reformatted: http://dx.doi.org/http://dx.doi.org/10.17632/gy7bfzcgyd.1
--
Shared datasets:
A more extensive description of the datasets in Mendeley would be useful. Currently, the description of data lists the 4 primary datasets, but a detailed description of all the shared files would be helpful. More detailed metadata in each file would be helpful, including a definition of all the acronyms and abbreviations used.


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: INDICATORS FOR THE USE OF ROBOTIC LABS IN BASIC BIOMEDICAL RESEARCH: A LITERATURE ANALYSIS
Review round: 1
Reviewer: 3

Output:
Basic reporting: In their paper entitled “Indicators for the use of Robotic Labs in Biomedical Research: A Literature Analysis,” Groth and Cox argue that the larger issue of reproducibility across life sciences research could be addressed by the use of “cloud labs.”  These new laboratories are built to fully automate certain biological research protocols.  According to the analysis by Groth and Cox, these newly arrived cloud laboratories can automate over 60% of the protocols in a subset of papers within the Elsevier collection.  The authors do not clearly claim that researchers should be using these cloud labs, but they suggest that using them for certain protocols will decrease the number of errors within the field and increase the reliability of scientific research.

While an intriguing concept, the paper as is does not warrant publication.  At this point it merely points out that certain laboratory methods can be automation, which is obvious to the reader.  To warrant publication, the authors must distinguish methods that can be automated AND effect the scientific conclusion of the paper from methods that merely can be placed on a robot.  This would be a worthwhile publication.
Experimental design: Point 1 – Definitions of terms

The authors must and clarify define various words used throughout the paper.  These include:

1.  "automated"
2.   A "task" vs. "pipeline.  Where automation is used and helpful, and when something is "automated"
3.  A "robot" vs. "robotic lab".  Robots doing automation are plentiful and prevalent, while cloud labs are not. It's not clear if robots constitute "automation" the same way robotic labs do.
4.  Automation of "technique" vs. "analysis.”  For example, 'microscopy' appears as an robotic method, but it is unlikely that all instances of microscopy automated both the image capture and image analysis.
Validity of the findings: Point 2 – Methods that could be automated do not seem to be the ones causing the reproducibly issues.

Before publication, the authors must break down methods that can and can not be automated, compared to whether these methods are likely to impact the results of the specific paper.  The authors list methods that could be automated by a cloud lab without any examination or discussion of whether automating these methods would have any impact on the final scientific result.  Within these, many methods either provide a binary response, and are quite robust to variation and interpretation, or are merely preparatory and the preparation methods are robust to variation.  For example, PCR is a robust technique that is usually used in a preparative manner, to obtain enough genetic material for a given experiment.  It is difficult to see how outsourcing this method to a CRO would in any way affect the outcome of the primary and important experiment.  The same thing could be said for many of the other methods the authors define as automated.  A stronger paper would refine further and remove these methods from the list of those that could be automated.  Then, a better discussion forms around the methods that can and can not be automated.

Point 3 – How is a fully automated CRO any different than a “cloud lab?”

Before publication, the authors must draw a distinction between the existing, fully automated CROs and a “cloud lab.”  Otherwise, the rest of the paper does not come from a position of strength.  The authors make a very good point that automation and use of CROs can increase the quality of lab research, but they take a naïve approach to the topic.  They are correct that fully automated CROs, or fully automated internal facilities, are the standard for industrial science, where reproducibility is paramount.  Where they fail to convince a reader is how these new “Cloud labs” are any different than existing CROs.  For example, Transcriptic is a fully automated laboratory that allows researchers to conduct protocols of their choosing.  In industry, however, it is widely accepted that a CRO is a fully automated laboratory that allows researchers to conduct protocols of their choosing.

Point 4 --  Analysis lacks depth.

It appears the analysis is a simple word count with little post processing. There is inadequate meaningful justification of this simple technique, or explanation of how the analysis goes further. For example, why was a technique selected that lacked recall? Why were only exact matches used? Why not use a hierarchical ontology for categorizing methods. Additionally, there appear to be substantial error rates in the characterization of technique usage.

Finally, there is insufficient characterization of the papers which did not list an automated method (38% of papers), or discussion of this metric. It is loosely suggested, from the introduction, that these papers are likely to publish a new technique, but this number seems too high.

Point 5 – There is an inadequate characterization of corpus

There is some statement about types of papers in the introduction (main question, part I), but types are never meaningfully characterized initially or analyzed sufficiently. Before publication, the authors should better describe the corpus used for analysis. More metrics, such as the number of papers which have a methods section, would illuminate possible skews in the analysis. The analysis would also benefit from a deeper survey of the types of papers included in the corpus, e.g. MCB, study, clinical, new technique, etc.

Point 6 – Various copy errors

There are various copy errors throughout, but they are not listed here, as the paper must change significantly to warrant publication.

Point 7 - Usefulness of Figure 1

Figure 1 shows several steps which really just reduces down to a single screen of selecting papers which appear in Elsevier.
Additional comments: None


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: INDICATORS FOR THE USE OF ROBOTIC LABS IN BASIC BIOMEDICAL RESEARCH: A LITERATURE ANALYSIS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The paper is generally well-written. A few typos I pointed out in the previous review still appear in the manuscript, although the authors say that they have been fixed. It might be a PDF conversion error, perhaps. The typos in the current revision are as follows:
- "-The list of papers and their DOIs is available" -> are available
-Typos involving"method" ("methodbut", "methodswithin", etc.)
- "It is an elegant yet straightforward protocol lends itself"-> "that lends itself"
- "due to it's vague usage" -> "its vague usage"

I also think it would be good to be consistent about the usage of the term robotic lab vs. robot lab.
Experimental design: I think the manuscript has been improved with the additional concept annotator and a more inclusive search strategy.
One remaining issue for me: I am not convinced that using simple string matching for the 34 (=107-74) unmatched methods would cause potential bias, as the authors argue in their response. These have already been identified as robotic methods by some external entity, as I understand, not by the authors. Therefore, I believe their use is justified, as it mainly addresses the shortcomings of MESH and would strengthen their findings.

It would also be good to give a sense of how accurate the concept annotators are on a benchmark corpus, if possible, in the lack of a ground truth for the task.
Validity of the findings: No comment.
Additional comments: No additional comments


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

Input:
Title: INDICATORS FOR THE USE OF ROBOTIC LABS IN BASIC BIOMEDICAL RESEARCH: A LITERATURE ANALYSIS
Review round: 2
Reviewer: 2

Output:
Basic reporting: There are several instances where two words are missing a space, for example:
Page 6/Line 168 and 170 methodsdetected should be methods detected
Page 6/Line 171 and 172 methodsper should be methods per

Otherwise, everything looks good, the paper is well written and referenced, and it meets all the standards for PeerJ.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: The only other minor issue is this URL still does not resolve for me:
http://dx.doi.org/http://dx.doi.org/10.17632/gy7bfzcgyd.1

This URL does work:
http://dx.doi.org/10.17632/gy7bfzcgyd.1


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: INDICATORS FOR THE USE OF ROBOTIC LABS IN BASIC BIOMEDICAL RESEARCH: A LITERATURE ANALYSIS
Review round: 2
Reviewer: 3

Output:
Basic reporting: See final noted.
Experimental design: See final notes.
Validity of the findings: See final notes.
Additional comments: The paper is much stronger and clearer now, but the analysis still leaves something to be desired.  If you look back on my initial concerns, they focused on whether automation of the tasks that the authors suggest, such as PCR, would have any major impact on the outcome of the research.  My opinion is that they would not.  The authors do not address this claim in their responses.  That is the major issue I still have with the manuscript.

I am not firmly against publishing the work, but do believe the tone of the paper needs to change.  After all, this is really a presentation of the workflows that are used in the literature vs the availability of these workflows at CROs or automated labs.  It is a survey.  Conjecturing that automation of these workflows will increase reliability in the scientific realm is not believable to me, and may not be for the reader either.  An honest and thorough address of the topics in my original review would flush a lot of this out.  Unfortunately, this did not occur.


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: VISUAL AND ACOUSTIC COMPONENTS OF COURTSHIP IN THE BIRD-OF-PARADISE GENUS ASTRAPIA (AVES: PARADISAEIDAE)
Review round: 1
Reviewer: 1

Output:
Basic reporting: This paper involves description of the little known male display behavior r of the Bird of Paradise genus Astrapia from videos take by the authors.  The detail of the description varies with species, the description of the Huon Astrapia has the greatest detail. The descriptions tend to be  detailed and in some cases very limited for some species  The authors cite the available literature. There are no hypotheses being tested as this is pure description and some speculation as to the behavior
Experimental design: This paper provides only descriptions of videos of male courtships and in one case a copulation with a female.  The methods are adequate to to allow descriptions where relevant videos exist.
Validity of the findings: The findings appear valid.  The first video of each behavior type and the behaviors described match.  No statistics are presented due to small sample sizes.
Additional comments: The manner in which the male behaviors are described are very mechanical.  While there is no doubt that males are following as sequence I would have found it beneficial to see these displays as interactive, and inclusive of the  female's behavior. In some instance her behavior is noted, but more detail would be of interest and important in interpreting the actions on video. Even saying that she is off screen would be useful in the early stages.   It would also be useful to have a short summary of the results of the behaviors being described at the beginning of the sequence. Courtships leading to copulations and those the do not are often somewhat different as are those in which young males may be involved.


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: VISUAL AND ACOUSTIC COMPONENTS OF COURTSHIP IN THE BIRD-OF-PARADISE GENUS ASTRAPIA (AVES: PARADISAEIDAE)
Review round: 1
Reviewer: 2

Output:
Basic reporting: This article meets the standards set out for basic reporting. However, I do think the introduction is exaggerated with respect to the importance and implications of this study.
Experimental design: This paper meets the standards set out for experimental design. However, there is no research question posed in this study. This work is simply a description of behaviors noted in videos present in a public data base. This paper does not present the results of a 'study' or 'experiment' or 'investigation' nor is there a 'research question'. It utilizes videos available in a public data base, and it describes behaviors that have not been described before.
Validity of the findings: It would appear that this study meets the standards for validity of the findings. The videos in the library at Cornell University are 'valid' and thus descriptions of behaviors observed in those videos are also therefore valid. But, again, this paper does not present the results of a study or research project.
Additional comments: I appreciate the value of the videos collected by one or more of the authors and it is very important that behaviors previously unknown are described. This 'ethogram' part of the current paper is fine. These behaviors and vocalizations are important to describe. But, that's all this paper is. It is a partial, incomplete, poorly documented ethogram of courtship behaviors based on video recordings. That's okay, but I beg to differ with the authors that these descriptions represent the courtship phenotype of this genus. I generally don't like that term courtship phenotype, but even if it is a good term the genus Astrapia does not have one courtship phenotype as suggested by the title and introduction. Each species would have its own courtship phenotype, and each species would exhibit considerable variation in that phenotype.
Specific comments:
1. The authors couch the introduction as it's important to study birds of paradise in order to understand how sexual selection promotes diversity. The notion that sexual selection promotes speciation is a hypothesis, not a well-accepted fact. It probably does, but it is certainly not widely accepted to do so. And, the data in this study have nothing to do with sexual selection. The data in this study are just descriptions of behaviors used in courtship. I think the introduction should be rewritten to emphasize how little is known about various species of birds of paradise and the importance of cataloging their behaviors so that comparative studies can be done. I think the authors are trying too hard to make this study seem relevant to sexual selection or behavioral ecology in general. This study has no relevance to sexual selection or behavioral ecology. It is relevant to the biology of birds of paradise and understanding the diversity of behaviors in that group. That's okay, but I think the authors should not try to overstate the importance of their data.
2. The authors should describe what is meant by 'core bird of paradise' or 'core bird of paradise genera'.
3. The authors conclude that there are considerably more behavioral components to the display of Astrapia species than previously known. Well, considering that there is not a single paper describing any courtship behavior in any species of Astrapia, isn't that obvious? What is the point of even saying this? If zero behaviors were previously described, and now there are 7 behaviors described, does that mean that there are many more behaviors than previously known? I'm not purposefully trying to be flippant, but my point highlights the point above that the authors are trying to make this partial ethogram into something it isn't. These behaviors are important to describe, but I encourage the authors to accept the extreme limitations of their data set and not to venture outside of that data set.
4. I would have appreciated a comparison of the display behaviors across the species. Perhaps there aren't enough videos of all species? But, I think the authors should try to compare the various display elements across the species that show them. Or, compare these behaviors to those seen in other genera, like Parotid that the senior author has studied extensively.


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: VISUAL AND ACOUSTIC COMPONENTS OF COURTSHIP IN THE BIRD-OF-PARADISE GENUS ASTRAPIA (AVES: PARADISAEIDAE)
Review round: 1
Reviewer: 3

Output:
Basic reporting: All good.
Experimental design: No experiments were conducted.
Validity of the findings: The authors have been very responsible in restricting the interpretation of their data to generalizations supported by video observations. I would actually prefer more analysis and speculation in conclusions.
Additional comments: The authors present some extraordinary observations of the courtship display behaviors of Astrapia birds of paradise. These birds are incredibly poorly known, and found in some of the most remote habitats on earth. Practically ever page of the manuscript elicited at least one involuntary "Holy shit!" from this reviewer. The effort required to obtain these data are amazing, and the novelty is beyond doubt.
The real contributions of this manuscript is to further broaden our understanding of the diversity of the displays of birds, and birds of paradise in particular.

I think that the manuscript could be improved with a little bit of a change in narration style or perspective. The authors have presented this manuscript as an example of video "data mining". Although I applaud the use of video vouchers to document the behavior, it is not as if the authors are recommending this as a research method. Unlike genbank or other data bases, one can't legitimately say, "Gee, let's mine this video collection for amazing and unexpected data on bird behavior!" Incongruously, the author's don't reveal that Scholes and Laman have spent nearly a decade scouring the forests of New Guinea painstakingly collecting these kinds of video data!

I think attempting to present behavior as a more modern, data-mining pursuit actually distorts and harms our understanding of the results. For example, we are told that certain perches are "practice" perches, but we don't know anything about why that judgment was made.  Because the results are not presented in terms of how many days were spent where and in what season of the year, etc., we don't know whether the lack of continuity in behavior was because the birds never returned to that perch again, or the researchers had to move off. That sort of thing happens a lot. The authors assume things from knowledge they have, but are not part of the 'data-mining' procedure, and this affects all of the results.

Do the authors really imagine that members of the public could "mine" this "publicly accessible" video collection, and do anything like this job of accurate job of analysis? Absolutely not! The difference between these alternatives, of course, is what is missing from the ms. Perhaps brief description of the field effort etc. that went into each batch of recordings, and some further details in supplemental files could address this problem accurately. But it is also one of intellectual stance that comes across throughout the ms.

Lastly, I think that the authors could do more to compare, or at least discuss, the elements of the behaviors that are shared or convergent with other birds of paradise. For example, the wing-shuffling mechanical sounds are shared with some species of Epimachus, no? What other birds of paradise perform these relatively rare inverted displays? In the realm of convergence, the Velvet Asity (Philepitta castanea) also does a sort of somersault display around the perch that could be mentioned. Is there anything about the display of A. mayeri that is specifically associated with its extraordinarily long, and derived white tail? Although these comments would be speculative, they would be very constructive. So the analysis at the end seems shorter than needed.

Miscellaneous comments (line numbers):

59- No "the" before Astrapia

94-98- Include number of males here.

160-161- What exactly is a pivot? Lots of side to side motions would not be called pivots, so this is unclear.

173- The phrase "a display that is called…" sound very Olympian, like the names of the displays are discovered. But the authors just made them up! Please use "that we call…"

200-01- a side to side rocking motion that  makes the tail bob up and down? How is that? Can you help a little more?
247- "Interactive observation (female)"  - Sounds like the name of an modern, avant garde painting. It's not even helpful because an interaction requires two individuals, and the sex of only one is identified. How about the straight up- "Male-female interactions" ?? Same goes for "Upright nape-peck (pre-copulatory)". (I can't wait to see that in a gallery in Soho!) Why not Pre-copulatory upright nape-peck ?
254- turn, not tern
279- I am sure that it is challenging to visualize, but I really recommend a sonogram of the shirk-shirk wing sound. Although it may look poorly, acoustical details can probably be extracted from it. I think that needs to be in, or its absence needs to be explained.
316, 318- Should be fig. 5, not 4.
602-3- I cannot visualize the bird and its parts in Fig 2C at all. What parts are wings or tails? Can the authors help with this- perhaps a little inset line drawing? Otherwise, this image is a blackhole.


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: GENOME-WIDE IDENTIFICATION AND CHARACTERIZATION OF GRAS TRANSCRIPTION FACTORS IN TOMATO (SOLANUM LYCOPERSICUM)
Review round: 1
Reviewer: 1

Output:
Basic reporting: 'no comment'
Experimental design: 'no comment'
Validity of the findings: 'no comment'
Additional comments: 1. In the part of Materials and Methods, your introduction needs more detail. I suggest that you
illustrate the detailed methods of sampling materials at different stages in order to explain the results at lines 328- 331.
2. In the part of Materials and Methods, please indicate the criteria of excluding acids.
3. The English language should be improved to ensure that your international audience can clearly understand your text. I suggest that you have a native English speaking colleague review your manuscript. Some examples where the language could be improved include lines 291, 296-298, 319,323, 353-358. And some other problems were revised in manuscript.
4. I commend the authors for their extensive data set, compiled analytical works. In addition, the results of manuscript is useful to information for the functional research in the future for tomato. But it is clearly written unambiguous language. If there is a weakness, its English language is not professional in the manuscript (as I have noted above) which should be improved upon before Acceptance.


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: GENOME-WIDE IDENTIFICATION AND CHARACTERIZATION OF GRAS TRANSCRIPTION FACTORS IN TOMATO (SOLANUM LYCOPERSICUM)
Review round: 1
Reviewer: 2

Output:
Basic reporting: The English language should be improved to ensure that your message is transported clearly. I suggest that you have a native English speaking colleague review your manuscript.
Some examples for the beginning of the Ms:
rational root patterning - radial
(42)The transcription factors are essential in functional genomics - reword
(47)The GRAS transcription factor is - you are talking about a gene family
(65) The functional localization of the motif - reword
(68) In addition, the N-terminal region of GRAS proteins in the DELLA subfamily contains
the other two conserved motifs ......., indicating that the N-terminal domains of GRAS proteins are variable - finding motives does not necessarily make them variable
(83) Hitherto, the RNA-seq is developed, following the function of GRAS genes, which are
deeply excavated - can RNA-seq lead to function?
(90) the inhibition of DELLA proteins was released immediately by the 26S proteasome - the degradation by the DELLA protein through the proteasome released the inhibition

Make sure all spaces are at the correct position and check for italic on the plant names.
(49) Arabidopsis(Arabidopsisthaliana) first Arabidopsis not italic.
I think Brassicaceae is more commonly used in contrast to Cruciferae.
Recheck the gene names: e.g. 265 Solyc090830.2.2
Some newer literature references on GRAS proteins seem to be missing. Especially the discussion on the evolvement from methyltransferases could be important for the analysis of conserved motives.
Fig. 1 (and others)  - please explain colour coding and add some more information to the legend.
Fig. 2 - might be too small writing for printing

As this is an interesting field and genome wide analysis could tell us much about understanding evolution and the role of these factors in different developmental stages this could be more clarified in the discussion.
Experimental design: GRAS sequences were extracted from Solanum lycopersicum but the expression data were from S. pimpinellifolium? Why were those uesed and is there a difference between the GRAS genes in both species?
(205) in some GRAS proteins were less than that in the typical GRAS
domain, such as Solyc04g011630.1.1 or Solyc06g076290.1.1genes....
Did the authors check if this is just an annotation problem or if these genes might be pseudo genes?
Validity of the findings: (220) Strikingly, some clades do not contain the members of GRAS proteins from Arabidopsis or rice; for instance, Gv6 and BolA groups. This might be attributed to the loss of the corresponding member following the separation of the last common ancestor. - is there any prove that it is a loss of this branch not a gain?

(320) We also determined that some genes present a time-specific expression, such as, in the stage of fruit ripening; several genes are expressed in the later stage. - This is an important finding and should be elaborated upon. Fig. 5, where this data is derived from, is not very easy to follow - perhaps some symbols of grouping to different stages whould make this easier to read and interprete. Are the genes listed according to their branch (that could be added for clarification) or was there any clustering performed?
As you state "As a whole, we found that the same group of GRAS genes shared a similar expression pattern..." this is not compehensible from the figure at first glance.
Confimation of these data via qPCR might be recommendable.

In 2015 Huang et al. have put together a genome-wide analysis of GRAS proteins in tomato and added also expression data. The authors should make it more obvious in how this study differs from the previous study.
Additional comments: No additional comments


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

Input:
Title: A COMPARISON OF CHLOROPLAST GENOME SEQUENCES IN ACONITUM (RANUNCULACEAE): A TRADITIONAL HERBAL MEDICINAL GENUS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is generally well written and, apart from some minor grammatical errors and ambiguous sentences as indicated below, the language used is clear to understand.
The introduction section has effectively been written, introducing all the aspects of the study and referencing previous studies on genus Aconitum. However, there is need for more details in order to support the need for further molecular systematics research.
The two most recent studies by Hong et al. (2017) and Kong et al. (2017) on phylogenetic reclassification (reconstruction) appear to have clearly outlined phylogenetic relationships within the genus Aconitum by using multiple nuclear and chloroplast markers.
The authors in the current study acknowledge the effectiveness of universal markers of cp genome to resolve phylogenetic relationships among species (line 64-68). However, they claim that there is need for further research using data obtained from whole genome (Phylogenomics). To support their claim the authors have stated in line 94-95 and 99-100, that there are some species whose positions are yet to be resolved. The authors should list examples of a few taxa whose phylogenetic positions are unclear and outline how the current data will resolve.
The cited literature is relevant and recent.
The reporting structure is in line with the standards of the journal.
Figures are well presented and of good quality.
Information on raw data deposition and availability has been given by the authors.
Experimental design: The design used here seems sound, replicable and in line with the research concerns highlighted in the introduction section. The research is within the scope of the journal.
Validity of the findings: The results presented here are reliable based on the experimental design. The results and discussion section is sound and the readers can be able to draw conclusions based on the results discussed here.
Additional comments: The manuscript is well presented. However, to ensure that international readers understand the intended meaning in some statements, I suggest you further review the manuscript. Below, and as highlighted in the attached pdf, I have listed some of the points that may need your attention. Please compare the suggested statements to the original ones.
Line 32
The length of the cp genome sequences was 156,109 bp for A. angustius, 155,625 bp for A. finetianum and 157,215 bp for A. sinomontanum.

Line 33
Each of the three species possesses 126 genes including 84 protein coding genes (PCGs).

Please use ‘’structural variations’’ instead of ‘’structure variations’’ to refer to changes in genome organization.
Line 40
In total, 50 simple sequence repeats (SSRs) were detected in A. finetianum and A. angustius, while 57 SSRs were discovered in A. sinomontanum.

43
A higher percentage of…

45
..will be of benefit for further/ will benefit further….

54
The cp genome in angiosperms is a circular DNA molecule with typically quadripartite structure

74
…possesses heterologous chromosomes and is suggested to be a hybrid of A. finetianum and A. sinomontanum.

80
In the past decades, the genus Aconitum was known as a taxonomically and phylogenetically challenging taxon.

86
…ITS, which suggested Aconitum to be a monophyletic clade and a sister group of Delphinium

103
We further compared

114
Fresh leaves were collected from A. angustius, A. finetianum and A. sinomontanum growing in a greenhouse at South China Botanical Garden, Chinese Academy of Sciences.

124
Genomic DNA was fragmented randomly and then the required length DNA fragments were retained by electrophoresis

The minimum numbers (thresholds) of the SSRs were set to be 10, 5, 4, 3, and 3 for mono-, di-, tri-, tetra-, and penta-nucleotides SSRs respectively.

134 comments
You sequenced and annotated three species, here you report four species. Please confirm if this is correct.

OGDRAW should be in parenthesis

194
…. by manually identifying the overlapping regions.

195
In order to further determine the draft genome, quality and coverage of each base position by reads remapping were double checked and corrected accordingly.

200
The chloroplast genomes displayed a typical quadripartite structure, including a pair of IRs (25,927-26,225 bp) separated by LSC (86,664-88,074 bp) and SSC (16,914-17,107 bp) regions (Fig. 1 and Table 1).

202-205
I suggest you use 1 decimal place instead of 2.
The GC content of the three species was 38.0%, demonstrating congruence to that reported in A. barbatum var. hispidum and A. barbatum var. puberulum (38.0%) of subg. Lycoctonum as well as in the species of subg. Aconitum (38. 0% or 38.1%) (Table 1).

206
Please avoid listing the names of the species again, when it is clear that you’re referring to them.
When duplicated genes in IRs regions were counted only once, each of the three cp genomes encoded 126 predicted functional genes, including 84 PCGs, 38 tRNA genes and four rRNA genes.

212
In the three studied species, and similar to most other plants species, the maturase K (matK) gene is located within trnK intron.

213
In the IR regions, the four rRNA genes and two tRNA genes (trnI and trnA) are clustered as 16S-trnI-trnA-23S-4.5S-5S. This is also reported in the cp genomes of A. barbatum var. hispidumand and A. barbatum var. puberulumas as well as in many other plant species

223-225
However, structural variations were still present in the LSC/IR/SSC boundaries (Fig. 2). The genes rps19-rp12-trnH and ycf1-ndhF were located in the junction regions of LSC/IR and SSC/IR respectively.

225-230
The rps19 gene crosses the LSC/IRa junction in A. sinomontanum, A. barbatum var. puberulum and A.barbatum var. hispidum of subg. Lycoctonum, as well as in A. jaluense, A. volubile, A.carmichaelii, A. kusnezoffii and A. monanthum of subg. Aconitum. As a result, the gene has apparently lost its protein-coding ability due being partially duplicated in the IRb region, thus producing pseudolized Ψrps19 gene.

253
The average nucleotide variability (Pi) value was estimated to be 0.00549, ranging from 0 to 0.03856, based on comparative analysis of sequence divergence of complete cp genome sequences of Aconitum species.

271
MISA identified 50 SSRs, with minimum 10 bp repeats in length, in both A.
finetianum and A. angustius, while 57 SSRs were detected in A. sinomontanum.

280
Remarkably the SSRs had a high A/T content with only seven SSRs, including (ATCT)3, (TTCT)3, (CTTT)3, (TAAAG)3, (TTTC)3, (ATAC)3 and (CATT)3, containing one C or G nucleotide.

294
The total aligned length with parsimony informative loci was 178,392 bp with 4,342 for the complete cp genome sequences, and 106,535 bp with 3,164 for PCGs, respectively.

300
Based on the phylogenetic tree, the tetraploid A. angustius was always closely related to A. finetianum, which is also supported by previous research

Figure 1.
One of the ycf15 duplicates, on the IR, is colour coded as ‘other genes’ while in table two the gene is listed under ‘’genes for photosynthesis’’. Please check alongside the partially duplicated gene of ycf1.Probably this is because the duplicates have been annotated on the same strand of the DNA molecule.

Figure 2.
Please check the use of ‘inverted’ in the title. On the same, kindly consider using ‘’IR regions’’ or just ‘IRs’ while referring to the two IRs rather than using ‘IRs regions’.


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

Input:
Title: A COMPARISON OF CHLOROPLAST GENOME SEQUENCES IN ACONITUM (RANUNCULACEAE): A TRADITIONAL HERBAL MEDICINAL GENUS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Please have a native English speaker revise the writing. Examples of mistakes include lines 26-27, 70, 80-81, 86, 107-108, 305. There are many others, these are some of the worst.
Experimental design: No herbarium specimen vouchers are cited. Many journals now require this for publication. Vouchers are essential for reproducibility, especially in taxa where identification is challenging.
Considering that chromosome number is the best way to distinguish two of the species, ploidy confirmation is also desirable.
Line 189 describes results from de novo assembly, while line 129 describes a reference mapping method. Which is correct?
The phylogenetic analysis describes 3 methods used, but only 2 trees are shown (Fig. 4A & B). The nodal support values are not identified.
Lines 295-297: The 2 trees shown are not “mostly concordant” since 4 nodes differ, and 3 nodes in 4B do not have high support values.
Figure 1 is not necessary, since the difference between the plastomes is shown in Figure 2. All other aspects of gene organization do not differ from published Ranunculaceae.
Table 2 is not necessary, since this is the typical angiosperm gene content and structure.
Validity of the findings: Most of the plastomes used in the comparative analyses are unpublished sequences downloaded from GenBank, with no attribution other than citing accession numbers. What evidence do the authors have that these unpublished plastomes are properly identified, assembled and annotated?
The comparative analyses fail to incorporate the Aconitum reclinatum plastome, recently published by the same authors. This is unjustified.
My recommendation is to remove the phylogenetic analysis, since it does not provide much new information beyond the results already published in the A. reclinatum paper, and limit the gene content/structure analysis to species with reliable published plastomes.
Additional comments: No additional comments


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

Input:
Title: A COMPARISON OF CHLOROPLAST GENOME SEQUENCES IN ACONITUM (RANUNCULACEAE): A TRADITIONAL HERBAL MEDICINAL GENUS
Review round: 2
Reviewer: 1

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


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

Input:
Title: A COMPARISON OF CHLOROPLAST GENOME SEQUENCES IN ACONITUM (RANUNCULACEAE): A TRADITIONAL HERBAL MEDICINAL GENUS
Review round: 2
Reviewer: 2

Output:
Basic reporting: I had recommended removing the phylogenetic analysis – but the authors kept it in the manuscript. If it is retained, I insist that the authors fully acknowledge the source of all chloroplast genomes, including those that are unpublished. I am in favor of open data, but this also requires full attribution.

Two citations were added for published plastomes (Lim et al., 2015; Choi et al., 2016) but these are not included in the literature cited.
The unpublished Aconitum plastomes from Korea need to include a citation of the authors listed in the Genbank records: “Kim, G.-B., Lim, C.-E. & Mun, J.-H. unpublished. Complete chloroplast genomes of Aconitum species from Korea. Obtained from Genbank on Date”

Voucher numbers have been added (from Genbank records) for the source specimens of the plastome sequences, but these are incomplete – we also need to know the herbarium where the voucher is stored. This is missing from Genbank and will need to be obtained from the submitters of those sequences.

The phylogenetic distribution of the pseudogenes should be described (now that the phylogenetic analysis is retained). Interestingly, only pseudo-infA corresponds to a clade (i.e. single pseudogenization). In the case of pseudo-ycf15 the 3 species A. monanthum, austrokoreense & A. chiisanense are not monophyletic.  This suggests the tree is incorrectly resolved – or less likely, the gene was lost once and then restored to a functional copy. These possibilities need to be discussed. Likewise, rpl16 was either pseudogenized twice, or restored to function once in subg. Lycoctonum.

“pseudolized” is not a word. Replace with pseudogenized.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: No additional comments


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

Input:
Title: A COMPARISON OF CHLOROPLAST GENOME SEQUENCES IN ACONITUM (RANUNCULACEAE): A TRADITIONAL HERBAL MEDICINAL GENUS
Review round: 3
Reviewer: 1

Output:
Basic reporting: The added text on the phylogeny of pseudogenes (lines 360-370) requires substantial English improvement.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The authors have adequately addressed my concerns.


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: MALE SEX PHEROMONE COMPONENTS IN  HELICONIUS BUTTERFLIES RELEASED BY THE ANDROCONIA AFFECT FEMALE CHOICE
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript is well written with a solid foundation of literature to motivate the research conducted within; figures are legible and appropriately explained in captions. I have no major concerns with the analyses or writing, but please go through the references for consistency in formatting, especially italicizing genus and species names.
Experimental design: The authors do a thorough job of investigating male pheromone production in three distinct ways, strengthening the conclusions to be drawn from their findings. Reporting of protocols is explicit and clear from data collection to software used in statistical analyses.
Validity of the findings: The authors present strong evidence for the existence of pheromones in mature males that enhance mating success. Results from the structural, chemical, and behavioral experiments work together to show that chemicals produced (or at least stored) in the hindwings of mature males contribute to reproductive success. I have only a few comments about the reporting of these results and their implications:
First, in L 333-337, the authors note that courting rates differed between control and treated males in one of the four species, yet they report percentages for successful matings pooling all tested species. What do the percentages of mating success look like when excluding the species in which control males courted more frequently than experimentally treated males?
Next, experimental addition of pheromones is the other side of the coin to experimental removal/blocking of such compounds. In L 422-424, the authors give the example of H. cydno males unsuccessfully courting heterospecific females. Assuming that the pheromone composition of H. cydno is made up of a handful of similar compounds to those studied here, how difficult would it be to synthesize and experimentally apply such compounds to these males to do a complimentary follow up experiment?
Finally, throughout this manuscript, the male butterflies are said to have both forewing and hindwing androconia. This is a reasonable assessment based on morphology alone, as Figure 1 shows sexual dimorphism in both wing pairs. However, the chemical analyses of different parts of the wings suggest that it is largely if not entirely the hindwing region that produces/stores pheromones. Furthermore, the behavioral studies only blocked regions of the hindwing manipulated males to demonstrate differential mating success. It seems that the dorsal hindwing is the key area for pheromone signals in these species. In light of these results, is it less appropriate to continue calling the forewing regions androconia? Perhaps a sentence or two could be added about if/how results presented here affect the classification of the regions on the forewing?
Additional comments: This manuscript and the research within are both of high quality and definitely suitable for publication. As you can see, my corrections and suggestions are all minor. At most, a couple of points could be clarified with another line or two of explanation in the text, but no additional analyses will be required. I have mentioned some suggestions above with specific line references, but please see the attached file for the full list of line-by-line 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: MALE SEX PHEROMONE COMPONENTS IN  HELICONIUS BUTTERFLIES RELEASED BY THE ANDROCONIA AFFECT FEMALE CHOICE
Review round: 1
Reviewer: 2

Output:
Basic reporting: In general, the authors use clear, unambiguous, and professional language throughout. Their introduction and background are sufficient, the literature is well referenced and relevant, and the article structure conforms to discipline norm.

The figures are relevant and of high quality, though S3 is highly relevant to the main text of the article, and should be included in the main text.

The raw data was also supplied.
Experimental design: The authors posed a study searching for the presence of androchonia in four populations of Heliconius butterflies, and tested whether the presence of the chemicals produced by these androchonia influence male mating success. This is a highly relevant and timely research question for speciation and mate preference work, as Heliconius butterflies are a model system for speciation research. Male preference for female wing color is heavily studied in this system, but, to date, very little is known about either female preference or the use of chemical signaling in Heliconius mating decisions. Therefore, this study has the potential to substantially broaden the scope of speciation research in one of the most well used study systems for reproductive isolation and population genetics research.

The characterization of the chemical compounds associated with the proposed androchonia is outside of my technical area of expertise, therefore I suggest someone else review those methods. However, they appeared clear to me, and detailed enough that I believe they could be easily replicated.

I do, however, have a few comments and concerns about the experimental design of the behavioral assays.

1) Given that the authors only recorded female behavior when males were courting, the authors should describe (or cite a source describing) male courtship in H. melpomene, H. erato, and H. timareta. Male courtship is a very important part of this study, and it is currently undefined. Please include.

2) I am concerned by the large number of failed choice assays in two of the populations (H. melpomene rosina and H. erato demophoon). The authors appear to have used observational data for a portion of the females who did not mate with either the control or the experimental male (and thus have not behaviorally exhibited a clear preference) to assess whether females behave differently around preferred or non-preferred males. However, as these females did not mate with either male, it is unknown which male they prefer, therefore their data may confound the results.

3) I am also slightly concerned about the small sample sizes used for the behavioral assays, given that behavioral data tends to include a large amount of individual variance. The sample sizes are fine for the binary mating outcome analyses, but may be too small to detect biologically relevant female behaviors when searching for female behavior specifically focused towards attractive or less attractive males. The authors do mention these low sample sizes in the results section, but they then over interpret these findings in the discussion.
Validity of the findings: The authors did a good job presenting their work in the context of published research on the role of chemical signaling in butterfly mate choice. Their histology and chemical characterization results are clear, and their mate choice study, though with small sample size, has clear results.

I am, however, concerned by the selection of which butterflies were used for further analysis of female behavior (which I describe in more detail in the general comments below), and the authors classification of these behaviors as rejection behaviors.

The authors describe all female behavior as rejection behavior, however they do not have supporting evidence that these behaviors are, in fact, rejection behaviors in Heliconius melpomene, Heliconius erato, or Heliconius timareta. The authors should take an unbiased approach when describing the female behaviors, and simply state that they observed and recorded four different female behaviors: flutter, wings open, abdomen lifted, and flying away. Unless there is another study in H. melpomene, H. erato, and H. timareta that I am not aware of which clearly shows that fluttering, wing opening, abdomen lifting, and flight happen at a higher frequency when males are courting females than when females are not being courted by males? Fluttering and wing opening are fairly common butterfly behaviors, thus the authors should justify their description of these behaviors as rejection behaviors, or use more neutral language.
Additional comments: The authors integrated an interesting set of chemical ecology and animal behavior studies to assess whether chemical signals on the wings of male Heliconius butterflies influence male mating success. In general, this is a well written paper describing a timely set of experiments. However, I have a couple of major concerns regarding the behavioral experiment, as well as concerns about data interpretation, which I detail below.

1) For both H. melpomene rosina and H. erato demophoon, most of the females did not mate during the two-day choice assay (as illustrated in Table 1). This suggests to me that there may have been something wrong with the set-up. Are the authors sure that the females were old enough to mate? Are the authors sure that the males were old enough to mate? While it is clear that the females that did mate preferred control to androchonia blocked males, I am a bit concerned by the shear number of failed mate choice trials. Particularly given the authors interpretation of female behavior during the observed portion of the choice trials.

Given that most H.m. rosina females did not mate, I find it unsurprising that the authors did not observe a difference in H. m. rosina female behavior around control or androchonia blocked males (as illustrated in Figure S3). In fact, the authors’ behavioral results, coupled with their finding that over half of the H. m. rosina females failed to mate with either the control or the androchonia blocked males suggests that either these females were not reproductive, or that the females did not find either male attractive. Either way, one would expect these females (who did not mate with either male) to treat both male forms equally. I suggest that the authors remove the behavioral data for the females that did not mate, and only compare the behavior of the females with known preferences (ie mating outcomes). Otherwise the authors are using their assumptions about female preference to define behaviors as rejection behaviors, instead of using actual preference data to assess whether females treat males they prefer differently from males they do not prefer.

2) The authors state that the absence of these chemical compounds in young males and older females suggests that the compounds are unlikely to have been sequestered from plants, but that logic seems a bit flawed to me (Lines 370-373). The compounds could be sequestered from plants in males but not females, and only be released in older males. In order to state that the compounds are unlikely to be obtained from direct sequestration of compounds from larval host plants, the authors need to show that males reared on different host plants produce the same chemical compounds.

This does not mean that I do not agree with the authors’ argument that these chemical compounds are important for mate acquisition. I think the authors have adequately shown that these chemical signals increase the likelihood of female acceptance. However, I do not think the authors have sufficient support for their statement in line 372 that there could be genetic control of the production of these compounds. Nor does there have to be genetic control of the production of these compounds for them to play a role in reproductive isolation- if the chemicals were sequestered from host plants, host plant differentiation could be associated with male chemical differentiation and consequent reproductive isolation.

Lines 394-401: I am confused as to why the authors expect females from different species and populations to exhibit the same behaviors when interacting with males. The authors found that females did exhibit population specific behavioral differences in response to preferred versus non-preferred males- why not discuss this further? This is a particularly interesting finding, given the small sample size (which the authors do discuss in their results). As I mentioned earlier, since the authors have not yet shown that these behaviors are, in fact, rejection behaviors (and their results here suggest otherwise), the authors should use a more neutral term to describe the documented female behaviors.

Minor Comments:

Line 193- the authors state that shortening extraction time did not influence results, but do not show the data or cite a paper to support this statement. This should be a relatively straightforward figure or citation. Please include.

Line 425-426: The authors state that male androconial compounds differ between H. timareta and H. melpomene, but this data appears to be unpublished. Is it currently in review? Will it be published soon? Can the authors support this statement with published data?


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: MALE SEX PHEROMONE COMPONENTS IN  HELICONIUS BUTTERFLIES RELEASED BY THE ANDROCONIA AFFECT FEMALE CHOICE
Review round: 1
Reviewer: 3

Output:
Basic reporting: XX
Experimental design: XX
Validity of the findings: XX
Additional comments: XX


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: MALE SEX PHEROMONE COMPONENTS IN  HELICONIUS BUTTERFLIES RELEASED BY THE ANDROCONIA AFFECT FEMALE CHOICE
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have addressed my concerns in their revision.
Experimental design: no comment.
Validity of the findings: The authors have satisfactorily addressed my previous concerns.
Additional comments: I like this study. It is integrative and timely.

I appreciate the revisions the authors made to the text.  Particularly their inclusion of separate analyses of the female behavior in successful and unsuccessful mating trials, the detailed descriptions of the behaviors of the butterflies, and their moving the figure of female behavior from supplemental to the main text.

The authors have satisfactorily addressed my previous concerns.


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: MALE SEX PHEROMONE COMPONENTS IN  HELICONIUS BUTTERFLIES RELEASED BY THE ANDROCONIA AFFECT FEMALE CHOICE
Review round: 2
Reviewer: 2

Output:
Basic reporting: I have only seen the revised version with responses to the previous reviewers. In my eyes this paper complies to all criteria, it is well written, well illustrated and both introduction and discussion are sound.
Experimental design: The authors have convincingly responded to the concerns raised by the previous reviewers and I have no additional comments concerning the experimental design.
Validity of the findings: The authors have perfectly responded to the concerns raised by the previous reviewers, and reformulated parts where a slight over-interpretation might have occurred. No additional comments from my side.
Additional comments: This paper accumulates an important amount of work on male sex pheromones and their role in mating in different Heliconius species/races. It is evident that certain behavioural data are difficult to obtain in rare species/races. But this does not at all reduce the value of the presented data.


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: HCV CORE ANTIGEN IS AN ALTERNATIVE MARKER TO HCV RNA FOR EVALUATING ACTIVE HCV INFECTION: IMPLICATIONS FOR IMPROVED DIAGNOSTIC OPTION IN AN ERA OF AFFORDABLE DAAS
Review round: 1
Reviewer: 1

Output:
Basic reporting: English language usage is quite OK, although a review could enrich the manuscript.
Experimental design: In this manuscript, Wasitthankasem et al propose the use of the core antigen of the hepatitis C virus (HCV Ag) as an alternative marker to HCV RNA when screening patients for HCV viremia.

Considering that: “Development of highly sensitive of HCV Ag quantification assays correlates well with and is comparable to HCV RNA(Bouvier-Alias et al., 2002; Ottiger et al., 2013; Florea et al., 2014). Therefore, HCV Ag can be used as a reliable marker for the diagnosis of active HCV infection and the evaluation of response to antiviral therapy (Mederacke et al., 2009; Rockstroh et al., 2017; Alonso et al., 2017).”, what is the originality, or even the main objective of the present work? I understand that authors are presenting specific data from a given human population, but they should keep clear what exactly is the novelty of their approach.
Validity of the findings: The data is OK and the experimental work seems to be well conducted, but while reading the manuscript I got a question: Since authors say that “The results of this study suggest that anti-HCV Ab tests had a fair correlation with HCV RNA and are appropriate for primary screening…” are they proposing HCV Ag testing ONLY as a “primary screening” that should later be confirmed through HCV RNA testing? In this case, the discussion about the costs/time needed to HCV RNA testing makes no sense… The proportion of patients that needed diagnosis confirmation through HCV RNA testing seemed still significant to me. Could the authors discuss that?
Additional comments: Some points can be addressed by the authors:

There are no reasons to include the following phrase “The remaining samples were HCV RNA-negative.” at the Abstract since authors claim that, amongst patients, 222 tested positive for HCV RNA. Actually, at this point, it is not clear if patients negative for HCV RNA are simultaneously negative to HCV Ag and/or to anti-HCV (which seems not be the case since the presented numbers could not totally overlap).
Authors mention that disease progression after HCV infection depends on different factors, but they do not present any follow up of the patients. It would be interesting to have some follow up data in order to actually evaluate the efficacy of the proposed diagnostics.
Authors claim that “All but two of the HCV RNA-positive subjects were reactive to HCV Ag (≥3 fmol/L).”. What happened to these two patients? Were they subjected to the same therapeutics as the positive patients?
Again considering these two patients, at the Discussion it is mentioned that both were HCV genotype 3, but the next paragraph starts saying that “This study demonstrated that HCV Ag showed excellent correlation with viremia irrespective (sic) of the HCV genotype…” In my opinion, these two assertions are conflicting. Please comment on that.
Are the authors planning to evaluate the results of direct acting agents (DAAs) therapy as a potential outcome in the present cohort (controlling for HCV genotypes, for example)?


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: HCV CORE ANTIGEN IS AN ALTERNATIVE MARKER TO HCV RNA FOR EVALUATING ACTIVE HCV INFECTION: IMPLICATIONS FOR IMPROVED DIAGNOSTIC OPTION IN AN ERA OF AFFORDABLE DAAS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Wastthanasem R et al report a study performed in 298 HCV-seropositive individuals to test the usefulness of HCV Ag as a marker to access active HCV infection in an HCV endemic region. Their findings suggest that HCV Ag is a good surrogate marker for HCV RNA.

English language and written is clear.

My only suggestions in regards to this work are that the authors include some newest references to improve the discussion and how their results relate to these publications. For example,
a) Hepatitis C virus core antigen assay: an alternative method for hepatitis C diagnosis.
Wang L, Lv H, Zhang G. Ann Clin Biochem. 2017 Mar;54(2):279-285. doi: 10.1177/0004563216661218.
b) Can Hepatitis C Virus Antigen Testing Replace Ribonucleic Acid Polymerase Chain Reaction Analysis for Detecting Hepatitis C Virus? A Systematic Review.
Khan H, Hill A, Main J, Brown A, Cooke G.Open Forum Infect Dis. 2017 May 26;4(2):ofw252. doi: 10.1093/ofid/ofw252.

Also, what is the author's opinion on how this marker could potentially work in patients receiving antiviral treatment in their population setting? (The Role of Hepatitis C Virus Core Antigen Testing in the Era of Direct Acting Antiviral Therapies: What We Can Learn from the Protease Inhibitors. Linh Thuy Nguyen, Emma Gray, Aisling O'Leary, Michael Carr, Cillian F. De Gascun, and Irish Hepatitis C Outcomes Research Network).

¶
Experimental design: No comment
Validity of the findings: No comment
Additional comments: I find this work useful since it provides more insight on the effectiveness of an alternative method for HCV diagnostics in regions or countries that may not afford full-scale HCV RNA testing.


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: HCV CORE ANTIGEN IS AN ALTERNATIVE MARKER TO HCV RNA FOR EVALUATING ACTIVE HCV INFECTION: IMPLICATIONS FOR IMPROVED DIAGNOSTIC OPTION IN AN ERA OF AFFORDABLE DAAS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The drafting of the introduction is redundant (second paragraph , line 48-56) with respect to  the use of serology as a standard marker for diagnosis and the need for the use of confirmatory techniques, as well as the disadvantages thereof, which is mentioned again in paragraph 4 (lines 71-76).

Due to a suggestion in the following section, I consider that the literature reference in line 87 and 95 is needless in that context, so I suggest replacing its justification in relation to the origin of the samples, which come from endemic regions of the infection, demonstrated in this literature reference (Wasitthankasem et al. 2017) .

References in line 372 and 441 do not have a DOI number.
Experimental design: In materials and methods are not described the evaluation of the combination of Ac and Ag tests to predict active infection. In table 3 , the results of HCV Ag and AntiHCV plus HCV Ag are exactly the same.

The content of the statement of line 101 is a description of a result, not of the methodology, should appear in results only.
Validity of the findings: The title of manuscript refers the implications for improve treatment option but there are only one paragraph  in the manuscript that mention therapeutic agents and does not make specific reference to how it impacts the use of the determination of the antigen in the treatment of the patient. Neither in the objetive, experimental design or results does contemplate the dynamics of the marker during the treatment; in the discussion are not discussed the implications that the use of the antigen could have like marker of monitoring in the patients.

There are others articles  with the same results that this manuscript and the authors do not let us known which is the importance of repeat this analysis.

Roberto Alonso et al. HCV Core antigen assay as an alternative to HCV  RNA quantification: a correlation study for assessment of HCV viremia. Enferm Infecc Microbiol Clin. 2017

H.A. Soliman et al. Significance of the hepatitis C virus core antigen testing as an alternative marker for hepatitis diagnosis in Egyptian patients. European Review for Medical and Pharmacological Sciences. 2015

Magali Bouvier-Alias et al. Clinical utility of total HCV core antigen quantification : a new indirect marker of HCV Replication. Hepatology. 2002

Van Helden J et al. Hepatitis C diagnostics: clinical evaluation of the HCV core antigen determination. Z Gastroenterol. 2014.

Chevaliez S et al. Clinical utility of hepatitis C virus core antigen quantification in patients with chronic hepatitis C. J Clin Virol. 2014.

Hadziyannis E, et al . Is HCV core antigen a reliable marker of viral load? A n evaluation of HCV core antigen automated immunoassay. Ann Gastroenterol. 2013

And the others cited in the manuscript.

The demographic data presented is not discussed and/or referred to as relevant to the purpose of the article. That is, the degree of fibrosis, age, gender or level of enzymes directly affect the determination of the HCV core antigen or what is the purpose of presenting them or having collected them in relation to the objective of the work? For example, in line 167, the associations between HCV RNA and elevated liver enzymes levels and advance liver stiffness are widely accepted clinical results, relevant for the HCV treatment and clinical management but irrelevant for the diagnosis of active HCV infection.

For the same reason I higly recommend removing Figure 1, because it does not present relevant data that are not addressed in figure 2. The objetive of this work is correlates HCV RNA  and HCV Ag, so the study universe is samples but not patients. Hence only is necesary known the total numer of Ac HCV positive samples that was used for the study.

In Discussion (lines 274-277), the justification described for the antigenic test refers to cost; should be more sustained with respect to an approximate cost of each of the tests or a percentage of total savings in the test algorithm used for a patient with active HCV.

Because the "Optional Screening Strategy" is not based entirely on the results obtained in this manuscript, it is suggested to give credit to the authors on which it bases its proposal. I sugest a statment like this "...These results together with previously reported evidence allow us to suggest a strategy...". On the other hand, the strategy does not contemplate the genotyping of the virus.
Additional comments: No comment


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

Input:
Title: HCV CORE ANTIGEN IS AN ALTERNATIVE MARKER TO HCV RNA FOR EVALUATING ACTIVE HCV INFECTION: IMPLICATIONS FOR IMPROVED DIAGNOSTIC OPTION IN AN ERA OF AFFORDABLE DAAS
Review round: 2
Reviewer: 1

Output:
Basic reporting: Authors adequately answered the questions raised by this reviewer.
Experimental design: The authors clearly stated the novelty of their approach – meaning, a cost and effectiveness comparison of the different methods of HCV infection detection, in an environment characterized by a high prevalence of HCV infection, in a low-income country.
Validity of the findings: No comment
Additional comments: Authors adequately answered the questions raised by this reviewer.
The authors clearly stated the novelty of their approach – meaning, a cost and effectiveness comparison of the different methods of HCV infection detection, in an environment characterized by a high prevalence of HCV infection, in a low-income country.
Also, the Discussion was restructured and the information specifying which patients would be tested by which detection method was added. Specifically, authors included that individuals who possessed anti-HCV antibody would be screened for HCV Ag. Only HCV Ag-negative samples should then be confirmed with HCV RNA-testing.
Although no follow-up data were presented in order to actually evaluate the efficacy of the proposed diagnostics, I understand that this was beyond the scope of this study. Also considering treatment, but now concerning the two patients that tested negative to the HCV Ag, the authors just explained that they were referred to the Thailand National Health Security Office as otherwise positive based on the RNA results (gold standard).
In summary, and as previously mentioned, I believe that the authors adequately answered the questions raised by this reviewer and that the modifications enriched the manuscript.


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

Input:
Title: HCV CORE ANTIGEN IS AN ALTERNATIVE MARKER TO HCV RNA FOR EVALUATING ACTIVE HCV INFECTION: IMPLICATIONS FOR IMPROVED DIAGNOSTIC OPTION IN AN ERA OF AFFORDABLE DAAS
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors have improved the manuscript. The English language is clear, references have been updated, and the structure is adequate.
Experimental design: The authors have clearly explained their methodology and work algorithm, which in turn is part of their proposal to screen for HCV using the viral antigen.
Validity of the findings: These points were covered by the authors and corrected for clarity as suggested by the reviewers.
Additional comments: As mentioned in the first review, this work is important because it offers an alternative diagnostic method for HCV screening, thus securing treatment of those who are unaware of their condition in regions of high endemicity.


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: HCV CORE ANTIGEN IS AN ALTERNATIVE MARKER TO HCV RNA FOR EVALUATING ACTIVE HCV INFECTION: IMPLICATIONS FOR IMPROVED DIAGNOSTIC OPTION IN AN ERA OF AFFORDABLE DAAS
Review round: 2
Reviewer: 3

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: The changes in title, introduction and conclusion are adequate and let known which is the importance of this study.

I only sugest that in order to unify the terms, use the term : "low- to middle-income countries  (LMIC)" in line 66 (introduction)
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: TRANSCRIPTOME DYNAMICS ALONG AXOLOTL REGENERATIVE DEVELOPMENT ARE CONSISTENT WITH AN EXTENSIVE REDUCTION IN GENE EXPRESSION HETEROGENEITY IN DEDIFFERENTIATED CELLS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript needs work on sentence structure. Specifically, the overuse of prepositional phrases makes the sentences very difficult to follow. I suggest that the writer limits the use of these phrases and the manuscript will be much more reader friendly.
Experimental design: The analysis seems sound, but the interpretations for what may be occurring within the blastema are overreaching and sometimes based upon speculation. Little is known about the cell heterogeneity across the time points studied and almost nothing is known about the chromatin structure in these cell type. The study is interesting and of value, but toning back the interpretation seems appropriate. The following suggestions point to examples where changes could be implemented.
Validity of the findings: -I am not disputing the possibility that gene expression heterogeneity decreases during dedifferentiation, but it is unclear if the gene expression measures utilized in this study can support this hypothesis. This argument is based upon several points:

1) Our understanding of cell dedifferentiation during limb regeneration is minimal, which is an assumption required for this analysis to be applicable. As far as I am aware, only one cell type, the fibroblast, is assumed to dedifferentiate during axolotl limb regeneration and the definition of this dedifferentiation is unclear. Could fibroblasts just be “activated” fibroblasts similar to myofibroblasts in mammals, yet have more capabilities for patterning. Is the level of dedifferentiated limb fibroblasts known? As far as I know it is not. The fibroblast population in the limb is a small proportion of the cells that make up the sample used for transcriptomic analysis. Could the conclusions made be a representation of gene expression not actually occurring in the dedifferentiated fibroblasts?

2) The sharp decrease in gene expression heterogeneity after injury does not necessarily represent dedifferentiation. For example, amputation leads to a retraction of muscle fibers and their decrease in expression of many muscle-specific genes, which is likely highly heterogeneous in its extent and temporal profile. This phenomenon would lead to high variability early on and decreased variability after the event occurs.

“Somehow surprisingly, not only cvGEBIs were significantly different for the expected timepoints, but they started being significantly negative as early as 1.5 days after amputation (Figure 1, and Table 1). If a reduction in gene expression heterogeneity truly reflected the presence of a significant number of dedifferentiating cells, these results would suggest that cell dedifferentiation leading to the formation of the blastema can be noticed transcriptomically considerably earlier than it can be defined morphologically.”
	-This statement assumes that dedifferentiation is the only transcriptional profile being 	collected, which is not the case. During this time, the inflammatory response, wound 	closure, and histolysis are all beginning to reside, which should also generate a decrease 	in transcriptional heterogeneity once they subside. I don’t think it is appropriate to say 	that the signature is due to dedifferentiation.

4) The interpretations made by studying cell heterogeneity could be innapropriate because the readout is the average signals generated from a mass of heterogeneous tissue including muscle cells, vascular cells, Schwann cells, epidermal cells, skeletal cells, and fibroblasts. Assume that the early blastema contains many different cell types, but may be different from sample to sample. Over time, the majority of cells in the blastema are of a single cell type, likely the fibroblast. This scenario would give the same gene expression heterogeneity profile seen here, but the interpretation would be considerably different than the one presented in the manuscript. Without single cell data, it is difficult to prove that the loss of gene expression heterogeneity demonstrated here is due to cell dedifferentiation.

-Can a sentence be included in the GO analysis stating that the genes represented in the mitotic re-entry category are significantly different than the chromatin organization category. Chromatin organization in terms of GO is often associated with the cell cycle instead of the euchromatic or heterochromatic nature of the chromatin.

-It is argued in the manuscript that chromatin architecture changes globally during regeneration. I am unaware of a study that demonstrates this to be the case. The author argues this point, but it is speculation until a study demonstrates this to be the case.

-Can the author provide evidence that 10 biological replicates is sufficient for testing heterogeneity of gene expression? They present data that lower biological replication is likely insufficient, but can an argument be made that 10 replicates is enough?

-The authors should make clear how the analysis presented here varies from the original Voss et al., 2015 manuscript.
Additional comments: The manuscript by Diaz-Castillo presents some interesting points on the general feature that dedifferentiation is associated with a loss of gene expression heterogeneity. The manuscript uses a deep transcriptional dataset of axolotl limb regeneration to study gene expression heterogeneity throughout the regenerative process. Although the analysis seems sound, the interpretations for what may be occurring within the blastema are overreaching and sometimes based upon speculation. Little is known about the cell heterogeneity across the time points studied and almost nothing is known about the chromatin structure in these cell type. The study is interesting and of value, but toning back the interpretation seems appropriate. The following suggestions point to examples where changes could be implemented.
Most points are covered in the above sections.


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: TRANSCRIPTOME DYNAMICS ALONG AXOLOTL REGENERATIVE DEVELOPMENT ARE CONSISTENT WITH AN EXTENSIVE REDUCTION IN GENE EXPRESSION HETEROGENEITY IN DEDIFFERENTIATED CELLS
Review round: 1
Reviewer: 2

Output:
Basic reporting: NA
Experimental design: This manuscript performs a set of investigations and provides empirical evidence for the hypothesis that dedifferentiated cells will lead to reduced gene expression heterogeneity. Motivation and problem are clearly described.
Methods are described with proper details, I would suggest to add more biological explanation for each metric used in the study.
Validity of the findings: An existing data set is used in the study.  The effect of the number of replicates is discussed, highlighting the importance of enough replicates.

Several different metrics (including proper statistical test) are used to analyse the data and derive final conclusions.
Additional comments: The manuscript presents empirical results for the hypothesis of reduced gene expression heterogeneity in dedifferentiated cells. Overall, the paper is well organized and presented. Conclusions are well derived from the analysis. My only suggestion is to add more biological meaning for the metrics used in the study.


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: TRANSCRIPTOME DYNAMICS ALONG AXOLOTL REGENERATIVE DEVELOPMENT ARE CONSISTENT WITH AN EXTENSIVE REDUCTION IN GENE EXPRESSION HETEROGENEITY IN DEDIFFERENTIATED CELLS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The author has made significant changes to the manuscript to make it easier to follow.
Experimental design: The experimental design was based upon a previously published study, which was strong.
Validity of the findings: My general concern in my original review was the interpretation of the findings. Many of the issues cannot be resolved without years of research in the field to determine the actual meaning of dedifferentiation and the cellular heterogeneity of the regenerating limb blastema. The Author has made significant changes to provide support for their idea of dedifferentiation and I accept the arguments made by the author.
Additional comments: The author has strengthened the manuscript through the changes made throughout the manuscript and their rebuttal to the reviewers is valid. I am comfortable supporting acceptance of the manuscript.


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

Input:
Title: TRANSCRIPTOME DYNAMICS ALONG AXOLOTL REGENERATIVE DEVELOPMENT ARE CONSISTENT WITH AN EXTENSIVE REDUCTION IN GENE EXPRESSION HETEROGENEITY IN DEDIFFERENTIATED CELLS
Review round: 2
Reviewer: 2

Output:
Basic reporting: The sentences are really difficult to understand. A native speaker is suggested to revise the manuscript.

cvGEBIs is the major concept for this paper. But it's not well described in the method. It would be nice to provide a formula or diagram to readers.
Experimental design: The idea of studying changes of expression heterogeneity is very interesting. However, the logic is not complete to get the conclusion.
Validity of the findings: The logic connection between extensive chromatin relaxation and generalized decrease in gene expression heterogeneity along with cell dedifferentiation is not clear. How extensive chromatin relaxation causes generalized decrease in gene expression heterogeneity is not explained in the background.

The normalization method strongly affect the detection of generalized increase in transcription. The author should do more research about it. Other wise it's really difficult to convince people that generalized increase in transcription doesn't contribute to the decreasing of expression heterogeneity.

The fact that genes have sharp decrease in gene expression heterogeneity between 1 and 1.5 days post-amputation are enriched in cell cycle and chromatin organization terms doesn’t suggest these two functional terms are the mechanism of decreasing gene expression heterogeneity. Instead the author should test if genes that are deferentially expressed post-amputation are enriched in these two functional terms.
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: INCREASING EVIDENCE THAT BATS ACTIVELY FORAGE AT WIND TURBINES
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: One concern about the experimental design is that methods for species identification for acoustic calls needs to be clarified on if all species were identified using auto-ID functions of the software or if there were comparisons with call libraries during manual identification of call files.

Another concern about the experimental design relates to the data collected from insect trapping being compared to genetic data of fecal and stomach contents.  It appears to me that insects from trapping were not identified to the species level using genetic analyses and therefore, those data can't be compared directly to species identification of the genetic material at the same taxonomic level.

See specific comments on the manuscript.
Validity of the findings: It needs to be clarified how fecal samples were collected with details of where guano was being obtained.  Were these guano samples in small piles or were there fecal pellets stuck to the turbine/door as if the guano was had fallen from a bat in flight.  Isopods discovered in the fecal samples, as found in the supplemental tables, raises the question on the validity of identified insects consumed by bats.  This is particularly so given that these arthropods are usually on the ground or under substrate and generally photophobic and unlikley to be attracted to the turbines themselves.  In light of this, there are possible explanations for its presence in your samples and the need for caveats.

See specific comments on the manuscript.
Additional comments: This is a great paper that uses a variety of methods to detect the presence of foraging behavior by bats at wind energy facilities!  However, I feel that there are some missed opportunities when you don't present more on the acoustic data for the other bat species that show a greater amount of feeding activity than hoary bats and red bats.

I do like the fact that there is a comparison of insects captured at the sight vs. the stomach and fecal samples of bats.  However, the resolution in species identification from the genetic analyses is difficult to compare to the trapped insects when the same methods aren't employed.

I think some of the conclusions related to your findings are fair to speculate but may not be the entire picture of what is happening in this system. I did play devil's advocate by pointing out other options or reasons for explanation that could also be possible.  These are addressed directly in the manuscript.