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: SEED BANK AND GROWTH COMPARISONS OF NATIVE (VIRGILIA DIVARICATA) AND INVASIVE ALIEN (ACACIA MEARNSII AND A. MELANOXYLON) PLANTS: IMPLICATIONS FOR CONSERVATION
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors built an interesting article comparing native and invasive species performance and conducted the discussion in a good way. Especially, the management topic provides information and alternatives to control and eradication of invasive acacias. Nevertheless, few improvements are needed in the article as you can see in the following recommendations and in the PDF file.

The introduction can be improved by adding a sentence in the first paragraph and a new paragraph with focus on management.

Regarding scientific names, look at the lines 176, 249, 310, and 325. I just recommend using the abbreviated names except for the first time in the paper and at the beginning of the sentences.

The supplemental material and the provided raw data is adequate. However, report the geographic coordinates datum in the header and withdraw the comment in the last line in S1.
Experimental design: The sampling design is clear and understandable when we use the Supplemental 2. Therefore, consider using this schematic drawing as a figure. Additionally, I would recommend giving the clear information whether all saplings within the one-meter sub-sample are considered as a focal sapling (between 187 and 189).
Validity of the findings: The section “Conservation implications” is very interesting. Nevertheless, a short change in the text order could reinforce the authors' suggestions about V. divaricate in the lines 349-350.
Additional comments: Could V. divaricate be a problem if used to control biological invasion since “Under natural conditions, V. divaricate typically occurs in dense monospecific stands along forest edges (forest-fynbos ecotone) after fire”? I recommend approaching this topic in the discussion (around lines 366-372, maybe).


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: CHILDREN’S PHYSICAL ACTIVITY AND SEDENTARY TIME COMPARED USING ASSESSMENTS OF ACCELEROMETRY COUNTS AND MUSCLE ACTIVITY LEVEL
Review round: 1
Reviewer: 1

Output:
Basic reporting: The English used throughout the manuscript is professional and generally clear and concise. However, some sentences contain grammatical errors (examples: line 61, 87) or are slightly long and sometimes hard to read (example: line 87-92). The manuscript would benefit from another proofread.

The background provided is sufficiently backed up with quality references and background and context is provided. Please add references to line 61 and 101. Also, the reference used in line 120 is inaccurately used; the references used only back up the first part of the sentence. Placing these references at the end of the sentence seems to suggest that previous research supports entire statement. Also, in line 244 is an adult reference provided whilst participants in the study are children; this should be noted.

The article has a professional structure and the figures and tables are clear. Raw data is shared and is clear.
Experimental design: The research falls under the aims and scope of the journal. The research question is well defined, relevant and meaningful.

The research is novel, interesting, and meaningful. Currently, accelerometry is the most commonly used measure of PA and SB, however it has it’s limitations. Therefore, it is important to compare this measure with other measures of PA and SB. The research conducted contributes to the knowledge around measure PA and SB. This has been clearly explained in the manuscript.

The methods used in the research were limited with regards to the following issues;
1)	Number of participants: Whilst 2 samples of participants were combined within this study (n = 11 and n = 14), samples were only combined in the "walking" task. The remaining tasks were different across the 2 studies and only assessed for either 11 or 14 participants. For example, the results in the sections ‘PA levels in specific tasks’, ‘PA levels during daily life’ and ‘comparison of different thresholds in ACC and EMG’ were therefore only based on 14 participants. Interestingly, the differences between ACC and EMG for “walking” was the smallest of all tasks (figure 1) – this is the only activity assessed in all 25 participants. The low number of participants should be noted as a limitation.

2)	Duration of tasks/Activities assessed: The activities assessed are very short in duration (all under 2 minutes). For ACC measures, data were summed over 15 second epochs (for all analyses other than the epoch length comparisons). In other words, the assessed tasks ranged in duration from 1 to 8 epochs. Please explain to what extend the provided %'s spent in certain intensities (presented in figure 2, for ACC) are representative for the actual % spent in intensities, or that combination of the short duration of tasks with relatively long epoch times might have limited the variation in %'s within the tasks. Interestingly, ACC values were emphasized over EMG values in the longer activities (swinging and trampoline jumping, line 327), and EMG values were emphasized over ACC values in shorter activities (crawling, squat, etc., line 325). Also, it was not fully clear to me whether the EMG data had been collected in shorter frequencies or with similar "epoch lengths". Did the researchers consider longer activities or analyses with event files rather than epochs? This should be stated as a limitation.

3)	The lack of validated thresholds for EMG in children. The EMG shorts have not been validated in children.  The authors recommend to use the ACC epoch length of 7.5s or 15s for close association with muscle activity based estimations of PA in children, however, given the methods to measure EMG in children have not been validated this might be premature. This has been mentioned in the discussion, but this could be extended.

The methods have been described in sufficient detail and could be replicated. Personally, I think the provided detail on the tasks (list of activities) is slightly too long and would fit better in an attachment. Most of the activities are easy to understand from the name itself and the extensive explanation is not needed within the manuscript.
Validity of the findings: Whilst I believe the research is novel and important, I think the recommendations made and conclusions drawn are too strong for the provided evidence. For example, in lines 418-419 and in lines 435-437. Given the previously mentioned methodology issues, I think it’s too premature to make these strong conclusions.

Hence, I think the recommendations and conclusions should be softened and more attention should be given to the limitations in the study design. I think the study could inform future studies on how to collect more evidence using similar approaches, rather than drawing conclusions and making recommendations based on just the results provided in the manuscript.
Additional comments: This study compared accelerometer (ACC) -derived and muscle electromyography (EMG) -based estimates of physical activity (PA) and sedentary time in common PA tasks and during daily life of children. The study combined data from 2 separate studies, N = 25 in total.

This paper is addressing an important research gap. Currently, accelerometry is the most commonly used measure of PA and SB, however it has it’s limitations. Therefore, it is important to compare this measure with other measures of PA and SB. The research conducted could contribute to the knowledge around measure PA and SB.

Whilst I think the findings of this study are important and novel, I think the recommendations made are premature. The participant number is low (especially because the participants of 2 studies are only combined in “walking”), the activities assessed were of short duration (i.e., containing only a few epochs) and EMG shorts thresholds have not been validated in children yet. Hence, I think the recommendations and conclusions should be softened and more attention should be given to the limitations in the study design. Given the novel techniques, I think the study could inform future studies on how to collect more evidence (e.g., bigger sample size) using similar methods. Alternatively, the current study could increase participant numbers and include longer activities.

Line: 67-68: Are there any systematic reviews which you could add here as a reference?
Line 79-80: Please explain this a little more, especially for researches who have not used EMG before.
Line 96-100: Very important information, I personally would prefer to read this earlier in the discussion.

Recruitment and study sample: It was not  clear to me how many participants dropped out due to unsuccessful ACC and/or EMG recordings in study 2 (i.e., missing data). Did study 2 actually include data from 14 participants or were the analyses only done for the participants who did not miss data (only 7 participants, based on line 146?)?

Line 162: Why did the authors use waist-accelerometers and not hip-accelerometers?

Table 1: Are these numbers means? Please provide this information.

Line 226: Why were the Freedson cutpoints not included in these analyses?

Line 242-243: Please add information regarding the validation here. I believe these references only included adult research. Alternatively, report that this is information based on adult research.

Discussion: The discussion is very long and could be shortened, for example by:
Line 334-341: This could be added to the introduction rather than the discussion.
Line 363-371: This is not very relevant to the current study and could potentially be removed from 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: CHILDREN’S PHYSICAL ACTIVITY AND SEDENTARY TIME COMPARED USING ASSESSMENTS OF ACCELEROMETRY COUNTS AND MUSCLE ACTIVITY LEVEL
Review round: 1
Reviewer: 2

Output:
Basic reporting: I found the standard of basic reporting to be good, with a sensible article structure. I could logically follow, from the raw data, what the authors did.

I believe the tables need to be reformatted to a higher standard than currently present. I also believe the table captions could be more elucidatory.

the results logically emerge from the methods, and methods from the aims/hypothesis.

I felt that the standard of English needs to be sharpened up throughout the manuscript. The introduction, in particular, I noted a number of occasions sentences were unclear, should be reworded or greater clarity is required. For instance; first line "a child has an inborn drive to be physically active" - very much a throw away sentence and should be cited and subsumed into the following sentence.
line 64 - examples of chronic diseases,
line 68 - "sedentary behaviour increases with age", you need to elaborate on this point, by what magnitude or we talking? I feel this is an important point given the importance of sedentary time/behaviour to this manuscript.
line 71 - specify what ages you mean with "school aged and youth".
line 72-76 - this read overly verbose, and could be much more concise
line 77 - reference use of accelerometry "widely".
line 77 - 80 - please be careful  with a very blanket description of accelerometry, there are many types of accelerometer available that work quite differently, including; MEMS, piezoelectric, piezo-resistive, capacitative.
line 83 - better description/definition of METS
line 86 - 88 - English standard is poor here
line 84 - by "observation", do you mean through tools like SO-PLAY? or just that MET values are apparent? please clarify
line 92 - 95 - please mention band-pass filters (high and low) also, these can have just as serious impact on accelerometry.

Within the abstract I would recommend you focus the discussion section on what "new" findings this work presents. Of particular interest is neuromuscular loading component. whereas referral to the impact of various cut-points is well-established.
Experimental design: the study is well within the scope of the journal, with a reasonably well defined.

I need the authors to reassure/explain to me (and the prospective reader) the rigour involved in combining 2 separate studies, with small sample sizes, looking at different activities and different ages.

furthermore, throughout the methods section (this may, in part, help address the previous comment), far more, explicit, detail is required. I am particularly au fait with accelerometry and sensors, but I struggled to follow precisely what happened methodologically. Please clarify in precise detail here. I think it is doubly important given the combination of 2 studies, and in order to facilitate replication, I recommend a very tight re-write of this section to remove all elements of ambiguity.
also curious why the use of Bonferroni? this is a very conservative?
Validity of the findings: I found the results to be logically inferred from the data in most cases.

However, in  the PA levels during daily life, the initial omnibus test (ANOVA) failed (non-significant), yet you continued to run a post-hoc test, I do not believe this is valid.

If you commence your investigation with the ANOVA and it fails, you have no license to continue investigating.

I think if you want to refer to the differences between the days, perhaps consider the use of effect sizes.

the rest of the results I was happy with.
Additional comments: Overall, I felt this meets all of the requirements and scope of the journal, with primarily only minor re-writing/editing in the manuscript. My only substantive concern was the methodological rigour, and clarity of the methods, which I would advise the authors address.


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: CHILDREN’S PHYSICAL ACTIVITY AND SEDENTARY TIME COMPARED USING ASSESSMENTS OF ACCELEROMETRY COUNTS AND MUSCLE ACTIVITY LEVEL
Review round: 1
Reviewer: 3

Output:
Basic reporting: This is an interesting paper that compares estimates of physical activity obtained from a hip-worn accelerometer with measures of muscular activity measured by EMG. This is done by comparing the measured intensity of various activities (using % of walking intensity, and % of time spent within each intensity category). There is also a comparison of different activity count intensity thresholds (cut-points) and different epoch lengths. The main conclusion from this work is that cut point/epoch decisions can affect results, and using the Evenson (2008) cut points with an epoch <15 s best represents the EMG data.

Although intelligible, some parts of the paper are hard to read, and there are numerous small spelling/grammar errors. For a reader to get the most out of the paper, it should be easy to read.  I feel it needs to be proofread by a colleague who is proficient in English. A few examples:

L31: and game of tag -> and a game of tag
L61 Physically active -> A physically active
L65 recommendations -> recommendations
L72-6 Very long sentence
L83 against derived from (doesn’t make sense)
L88 has been reported to be used -> have been reported and used
L87-92 Very long sentence
L92 Besides of the cut-off  -> Besides the cut-off
L139 volunteered to -> volunteered to participate in
L140 were finally included in the final sample -> were included in the final sample
L430 reference error
Etc.
Experimental design: In general, the study is interesting, but the rationale for undertaking such work isn’t well articulated. I understand the purpose of the study is to compare the X6-1a accelerometer with EMG, but why this is important, the knowledge gap it fills, and how it will be useful is not well defined. In the introduction, the problems associated with count-based cut points are highlighted, particularly the inability to detect activity type and posture (i.e., standing vs sitting). These issues have been well publicised over the last 10 or so years (which is why much recent work has been moving away from this approach altogether). It is true that EMG provides a direct measure of the electrical activity of the muscle, and may thus better represent low intensity and sporadic activities. However, these two techniques are fundamentally different. Is this study attempting to validate the X6-1a accelerometer using EMG as the criterion measure? Or simply highlighting issues with cut points? Or is it proposing that EMG is an alternate/better/different measure than accelerometers? This should be clarified.

A few small comments about the methods:

Only the Evenson cut points were tested at different epoch lengths. What was the rationale for choosing these and not the other cut points?

Why was walking chosen as the activity upon which to normalise the data? Would sitting be more intuitive?

As pointed out in the introduction, the distinction between sitting and quiet standing is important. Is there a reason that quiet standing was not included in the activity protocol?

I wonder if a measure of agreement (e.g., kappa coefficient) would be useful for interpreting how these intensity categories align?
Validity of the findings: A potential problem with the design of the study is that you are using an accelerometer that may not be compatible with the cut point thresholds you are using. Most of these cut points were developed for ActiGraph counts (which are derived using a proprietary algorithm), using the vertical (y) axis only. I haven’t seen the X6-1a accelerometer in the literature before. Your treatment of raw accelerometer data to derive counts is not fully explained, and this sensor uses a different sample rate and different filtering techniques compared to the ActiGraph. I see you have mentioned this in the study limitations, but the validity of all the results you have presented are based on how closely the X6-1a counts represent the ActiGraph counts. Do you know of any previously published work that can demonstrate their comparability?

It is unclear how the EMG data were categorised into four intensity categories. From L248-252: < 3 μV is sedentary, mean during walking is light/moderate, and this doubled is moderate/vigorous. This is three categories, how did you separate light from moderate, and moderate from vigorous? Did you measure EMG during standing and take 90% as sedentary? Similarly, almost half of the data in study 1 and 2 was lost due to insufficient EMG signals. What is the validity/reliability of the EMG shorts? Particularly in 6-9-year-old children. This may seem trivial, but all the comparisons you make in this study are dependent upon the accuracy of these EMG data processing decisions.
Additional comments: To summarise: a thought-provoking paper that is a little unclear in what it set out to achieve. It needs clarification in several areas (particularly the validity of methods) before it will serve as a meaningful publication for others.


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: CHILDREN’S PHYSICAL ACTIVITY AND SEDENTARY TIME COMPARED USING ASSESSMENTS OF ACCELEROMETRY COUNTS AND MUSCLE ACTIVITY LEVEL
Review round: 2
Reviewer: 1

Output:
Basic reporting: In general the English used throughout is professional.
Whilst the authors mention that a proofread has taken place, the manuscript still contains grammatical errors and long sentences. For example:
Line 45-47: "During day with and without exercise ACC resulted in greater proportion of light activity (p < 0.01) but smaller proportion of moderate activity compared to EMG (p < 0.05)."
Line 104-107: "It is important to note that during early years not only the cardiorespiratory (metabolic) but neuromuscular system in particular plays an important role because a major contributor to the development of motor performance, fitness, as well as proficiency of gross motor skills, is the ongoing neuromuscular development (Haywood & Getchell, 2014)."
Please ensure that the manuscript gets another proof read to address the missed errors.
The background provided is sufficiently backed up with quality references and background and context is provided. The article has a professional structure and the figures and tables are clear. Raw data is shared and is clear.
FinalComments_response_v2.docx: I would like to recommend the authors to provide some more guidance through the response document, for example through page and line numbers referring to the changes made. It was at times hard to find the addressed comments in the actual manuscript and I might have potentially missed valuable changes.
Experimental design: The research falls under the aims and scope of the journal. The research question is well defined, relevant and meaningful.
In my previous review, I expressed some concern regarding the duration of tasks/activities assessed in the previous manuscript. It is now clear to me why the choices were made and how the duration was influenced my certain factors. Thanks for clarifying this.
In general, I do think that the authors have provided a more comprehensive explanation about the methods and experimental design and this section has much improved. However, I still have some issues with the manuscript, which I have mentioned below.
Whilst the authors mention that they are aware of the small sample size, they only added limited text about this in the discussion (a small change in line 516). Some more specific limitations and potential implications for future research with a higher sample size could be added. The authors mention that an ongoing study will include more children, at the moment I do not understand in what areas that study will be improved/innovative compared to the current study and why the choice was not made to pool this into one study. It might be a good addition to further expand what future studies should incorporate. Did the authors contemplate classifying this study as a pilot study?
In the previous review, I asked for some clarification about epoch lengths/sampling rates:
-	Comment: Also, it was not fully clear to me whether the EMG data had been collected in shorter frequencies or with similar "epoch lengths". Did the researchers consider longer activities or analyses with event files rather than epochs? This should be stated as a limitation.
The authors answered the comment as follows:
-	[R]:  EMG and ACC were always analyzed over the same duration of the task (table 1). In this manuscript we have used the traditional counts-based analysis for ACC. Although ACC is collected with higher sampling rate, the data is reduced by using certain epochs. In future it would be good to use methods allowing raw data analysis (e.g. Vähä-Ypyä et al. 2015). EMG, is also typically analyzed in some epochs, e.g. average rectified value of 1 s is typically used for maximal voluntary contraction. In the current methodology, the available minimum signal is average rectified value every 40 ms. By taking a mean value of this for the duration of each task is not different if we had first averaged it in 1s windows and then during the entire duration of the task. Thus, while we may perceive the “effective epoch” length of ACC and EMG being different, by changing EMG processing we do not gain differences but ACC should be completely analyzed using different principles. In the current manuscript we chose to report ACC in counts that is the current standard.
In addition, this was stated as responses part of another reviewer’s comments:
-	For example, we found some sporadic activities (standing long jump, single leg hops, and jump for height), which EMG presumably results in a more realistic representation of energy demands while ACC counts summed over the duration dilute the effect (although ACC data processing issues are interrelated to this problem but not dealt with comprehensively in the manuscript).
Based on the previous comments and responses, it is still not clear as whether the choice of ACC counts in combination with EMG was compatible. Whilst I acknowledge that my lack of knowledge about EMG might be partially why this is still unclear, I do believe that this should be further explained to the reader also.

Whilst the authors have acknowledge in their manuscript that validation work is currently in progress, this does not cover the current research and is obviously depending on the results of this study. Are any unpublished results available which could serve as a justification for the chosen methods?
Validity of the findings: The recommendations and conclusions are slightly softened and more attention should is given to the limitations in the study design. Given the issues in the methodology, I still think that the results and conclusions are quiet strong. I think the paper could serve more as exploratory work informing future studies.
One minor comment regarding the following response:
-	[R]: We have been modified texts (original lines 418-419 and lines 435-437) accordingly.
I was initially unable to find these lines in the current manuscript. I recommend to provide line numbers of the newest manuscript rather than the original manuscript.
Additional comments: Most comments have been addressed appropriately and the explanation was clear, thank-you.
Nevertheless, there were still some grammatical errors throughout the manuscript. My biggest concern is the fact that the EMG method used is not validated in children yet. Whilst it is great to see that the authors are currently working on the validation, I think it would be really valuable to gain research of that research and implement this into the current paper. That would strengthen the current paper a lot and justify the drawn conclusions. Given the issues in the methodology, I still think that the results and conclusions are quiet strong. I think however that the paper could serve as exploratory work informing future studies.


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: CHILDREN’S PHYSICAL ACTIVITY AND SEDENTARY TIME COMPARED USING ASSESSMENTS OF ACCELEROMETRY COUNTS AND MUSCLE ACTIVITY LEVEL
Review round: 2
Reviewer: 2

Output:
Basic reporting: Thank you, to the authors, for diligently and forthrightly answering my own and the other reviewers comments. I found your rebuttal to logical and agreeable. As such, I found the basic reporting to be of a good standard.
Experimental design: The authors did a great job here of refuting some of the edits/comments put forward by the reviewers. In doing so, you have assuaged any doubts in my own mind, and am more the happy with this section.
Validity of the findings: all fine here. The authors, again, respectfully and soundly rebutted all comments.
Additional comments: Thank you for carefully attending to all of my own and other reviewers comments. I hope you feel/agree that the comments were fair and warranted. I also hope you feel that they have helped improve the manuscript. Following your diligent and soundly written responses, I am more than happy to suggest acceptance for publication of this novel work. Well-done, and I can't wait to see what more comes from this line of inquiry.

Dr Cain Clark


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: CHILDREN’S PHYSICAL ACTIVITY AND SEDENTARY TIME COMPARED USING ASSESSMENTS OF ACCELEROMETRY COUNTS AND MUSCLE ACTIVITY LEVEL
Review round: 3
Reviewer: 1

Output:
Basic reporting: In general the English used throughout is professional.
Sufficient references and background provided.
The article is structured professionally.
Experimental design: The research falls under the aims and scope of the journal. The research question is well defined, relevant and meaningful.
Validity of the findings: The authors have added more emphasis on that this is an exploratory study, conclusions are  softened, and more attention is given to the limitations in the study design.
Additional comments: I am satisfied with the authors' responses.


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: COMPREHENSIVE ANALYSIS OF METASTASIS-RELATED GENES REVEALS A GENE SIGNATURE PREDICTING THE SURVIVAL OF COLON CANCER PATIENTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Overall experimental designs are too easy to make a conclusion. Just gene sequence screening based on computer simulation is not enough to draw a conclusion. It it necessary to do more in-depth bench research.
Experimental design: We would expect more deep experimental design for the research in addition to in-silico experiments.
Validity of the findings: Current findings are not sufficient to support the conclusion mentioned in the manuscript.
Additional comments: I would not accept this manuscript.


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

Input:
Title: COMPREHENSIVE ANALYSIS OF METASTASIS-RELATED GENES REVEALS A GENE SIGNATURE PREDICTING THE SURVIVAL OF COLON CANCER PATIENTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: see below
Experimental design: see below
Validity of the findings: see below
Additional comments: The authors have analyzed datasets of primary and metastasis tissue of colon cancer patients and identified genes that are crucial to the metastasis and survival of colon cancer.
Major comments:
1.	Although the findings of this study have implication for colon cancer diagnosis and therapy, it is lack of functional validation of the target genes. This is a major limitation of this study.
2.	The authors should provide more detailed introduction and discussion on each of the four hub genes as well as the six genes for prediction of overall survival of colon cancer, such as biological function, its implication in cancer development, and literature report, etc.

Minor comments:
The language of this manuscript is poor to follow. Some typical language mistakes are shown below, as well as suggested changes.
1.	Change the title to “comprehensive analysis of metastasis-related genes reveals a gene signature predicting the survival of colon cancer”
2.	Line 25: change to “the genes that are altered during…”
3.	Line 26: add “are” after “that”
4.	Line 37: change “used” to “using”
5.	Line 39: change “demonstrate” to “has demonstrated”
6.	Line 40: change “involving” to “involved”
7.	Line 257: change “screen” to “has screened”


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: COMPREHENSIVE ANALYSIS OF METASTASIS-RELATED GENES REVEALS A GENE SIGNATURE PREDICTING THE SURVIVAL OF COLON CANCER PATIENTS
Review round: 1
Reviewer: 3

Output:
Basic reporting: .
Experimental design: .
Validity of the findings: .
Additional comments: Authors in this study has screened gene profiles involved in the metastasis of colon cancer and further identified four genes. They also identified and further validated six-gene signature that could be served as an indicator to prognosis colon cancer. Overall, this type of study will help to identify new therapeutic targets for the genes that are not yet proved to be associated in colon cancer metastasis. All in all, it is an interesting study, however, following concerns should be addressed by the authors before this work gets published.

1.	The manuscript is carelessly prepared, with numerous spelling, grammar, and formatting errors. It is not suitable to be published at the current version. Below are few weak sentences I found:
Line-62:  `need to further study`
Line-146: `that relevant with`
Line-257; 1a gene profiles`. Etc.

2.	Please rewrite the abstract. The following sentence is confusing –
` A gene signature was developed using the genes related to the overall survival (OS) of colon cancer patient in TCGA dataset. The prognostic value of gene signature was confirmed in validation dataset with 390 colon cancer patients`.


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: COMPREHENSIVE ANALYSIS OF METASTASIS-RELATED GENES REVEALS A GENE SIGNATURE PREDICTING THE SURVIVAL OF COLON CANCER PATIENTS
Review round: 2
Reviewer: 1

Output:
Basic reporting: see below
Experimental design: see below
Validity of the findings: see below
Additional comments: The authors have properly addressed all questions brought up in the first round of review. The manuscript is in good condition for publication.


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

Input:
Title: COMPREHENSIVE ANALYSIS OF METASTASIS-RELATED GENES REVEALS A GENE SIGNATURE PREDICTING THE SURVIVAL OF COLON CANCER PATIENTS
Review round: 2
Reviewer: 2

Output:
Basic reporting: Authors addressed all my concerns
Experimental design: Authors addressed all my concerns
Validity of the findings: Authors addressed all my concerns
Additional comments: Authors addressed all 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: OSTEOGENESIS IMPERFECTA: POTENTIAL THERAPEUTIC APPROACHES
Review round: 1
Reviewer: 1

Output:
Basic reporting: This is a well written review article with clear, unambiguous, professional, and technically correct text.
Literature references and contexts are sufficient.
The structure of the article is well format.
This review paper contains a board and extensive on Osteogenesis Imperfecta, bringing useful therapeutic approaches especially for dental practitioners.
I would recommend publication as it unites clinical dentistry with and extensive information in medical research.

As the reviewer, my only criticisms are;
1.	Line 46, (sentence)…in the body. Could the authors indicate one or a few references? For instance review articles or about the genetic basis of OI (COL mutations) - useful as PeerJ is a multidisciplinary journal.
2.	Line 129, please consider replacing/spelling the abbreviation of “VDO” as I could not find this full name in the manuscript
3.	Line 131, I am not quite sure about “Establishing a dental home”. Could you please clarify?
4.	Line 138, line-paragraph is broken.
5.	Line 191, the word “Osteogenesis Imperfecta” is not in abbreviation. Is it a mistake?
6.	Line 218, “Type” - “t” in the lowercase.
7.	At references section (line 293-438), there were some journals using the full name and some were not. Please do these consistently regarding the journal format.
8.	General comment for Figures: there is no mention of the origin of the pictures/patients shown (from literature? or more likely from the authors clinical archives?) This should be clarified - iconographic sources should be indicated.
9.	Figure 2, could you please add more precise explanations such as “Panoramic radiograph of a patient affected by OI type III with missing teeth and DI”?
Text and letter L (bottom right) should not appear on Figure.
10.	Table 1, it would be complete if you could insert “Type V: Moderately deforming” (from Rauch F and Glorieux FH, Lancet 2004) in your table because it was missing.
Experimental design: This review article contains both literature articles and their own data with a comprehensive and coverage of the OI.
The organization is logical and simple for general practitioners.
Validity of the findings: The conclusions were appropriately stated and supported by the results.
Additional comments: This review article has collected scientific and clinical relevance of OI. Authors recommended therapeutic approaches respectively on each clinical manifestations of disease. These data indicate that a multidisciplinary team approach is favored in moderate and severe cases as the variability in the degree of severity of OI patients may vary the outcome of treatments.

Overall, this is a well-organized and precise therapeutic guidance for all health professionals especially for dentists. Background evidence is solid and well presented. In addition, the manuscript is clearly written in professional, unambiguous language. If there is a weakness, it is generally in the “Basic reporting” 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: OSTEOGENESIS IMPERFECTA: POTENTIAL THERAPEUTIC APPROACHES
Review round: 1
Reviewer: 2

Output:
Basic reporting: Clear description of the disease (Osteogenesis imperfecta) of clinical interest.
good reason for this review with an adequate introduction of the subject.
Names of the gene (COL1A1 and COL1A2) should be put in italic.
Abstact: line 32: simple extraction can be performed after multi-disciplinary concertation
Experimental design: Exhaustive literature review in the field of osteogenesis imperfect, regarding the clinical, phenotypic and therapeutic aspects. Sources are well cited and recent concerning the clinical studies of biphosphonate treatment effects on jaw bone and implants treatments.
Validity of the findings: Interest of cone beam computed tomography exams could be discussed in the phenotypic characterization of the disease and the pre-surgical imaging, before implants of orthognathic surgery.
Use of zirconia preformed crowns in temporary dentition for esthetic rehabilitation of anterior teeth and also for posterior treatments could be more discussed.
Conclusion coud also open on potential new pharmacological treatments of OI.
Additional comments: line 152: full coverage is preferred when clinical or radiological signes of post-eruptive breakdowns are diagnosed.

line 155: discussion of the clinical difficulties for endodontic therapies in OI patients

line 261: Discuss the risks of biphosphonate treatment withdrawing for OI patients

line 270: add the exhaustive pre-surgical clinical and radiological examinations before implants therapy

line 273: add the number of implants placed in the study and the clinical situations of the patient (number of missing teeth)


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 BUOYANCY, BALANCE AND STABILITY CHALLENGE TO THE HYPOTHESIS OF A SEMI-AQUATIC SPINOSAURUS STROMER, 1915 (DINOSAURIA: THEROPODA)
Review round: 1
Reviewer: 1

Output:
Basic reporting: Clear and unambiguous, professional English used throughout.

Literature references, sufficient field background/context provided.
Appears so, but note that I am not a Spinosaurus expert.

Professional article structure, figs, tables. Raw data shared.
Structure is good. (Small point: LL 219 to 233 might be more logically placed in the methods section.)
Figures good.
Data sharing is adequate - but see comments below under Methods.
Experimental design: Original primary research within Aims and Scope of the journal.
Yes

Research question well defined, relevant & meaningful. It is stated how research fills an identified knowledge gap.
The study addresses the problem of reconstructing the Spinosaurus, which has previously been described as a fully aquatic predator. By using a well proven modelling approach, the author throws considerable doubt upon this view.

Rigorous investigation performed to a high technical & ethical standard.
The modelling approach has been used by the author in other published studies and appears to be robust and reliable. As I do not have access to the modelling software, I cannot confirm this.

I have two points related to the modelling, which are really my only significant comments on the paper:

1) It is incorrect to say that “The second criterion was that the centre of mass (CM) and the centre of buoyancy (CB) be either almost coincident, or that the CM lie below the CB, in order that the model not capsize.” Ship designers have known since the 1730s (see Ships and Science by Larrie D Ferreiro, chapter 4) that the stability of a floating body is determined by the height of the metacentre above the centre of gravity, where the metacentre is the point where the line of action of the buoyancy force crosses the centreline as the body is inclined laterally (or indeed longitudinally). The CM can be above the CB and a ship will still be stable (indeed, this is the case for the great majority of vessels.) This is described in detail in Comstock 1967 (Chapter 2) but can be found in any textbook on ship or boat design.

It would be useful if the author were to calculate the lateral stability of the models and discuss the results. I imagine it would be a simple matter to adapt the software to calculate the second moment of area of the water-plane and thus the location of the metacentre.

2) Sensitivity. The author describes his assumptions in considerable detail and provides good justification for them. However, they can only ever be informed estimates, so it would be helpful if some indication of the sensitivity of his results to his assumptions were given in the text.

Methods described with sufficient detail & information to replicate.
Replication would require access to the PV-Wave program, which I do not have. However, all the indications are that the author has provided sufficient data for replication to be possible for those with access to this program.

References

Ferreiro, L. D. 2007. Ships and Science: the birth of naval architecture in the scientific revolution, 1600-1800. MIT Press, London.

Comstock, J. P. (ed) 1967. Principles of Naval Architecture. SNAME, New York.
Validity of the findings: Data is robust, statistically sound, & controlled.
See comments above re sensitivity and need to discuss lateral stability.

Conclusion are well stated, linked to original research question & limited to supporting results.
Yes
Additional comments: From a technical, biomechanical perspective this very well argued piece of work. I am not very knowledgeable about the Spinosaurus debate, so cannot useful comment on that aspect of the work.

There are a few small typos etc:

The caption for Figure 5 contains an error. Presumably 9360 kg, not t!
Figure 5 Floating theropods with masses ranging from 10.3 kg to 9360 t

There are a number of random extra spaces (and missing spaces) in figure captions, also in Abstract. This may be an artefact of the conversion to PDF?Some species names not italicised. Most of the relevant text is copied below.

large predatory dinosaur Spinosaurusaegyptiacus proposed

However, similarly detailed models of another spinosaurid Baryonyx ( Suchomimus ) tenerensis, along with models of the more distantly related Tyrannosaurus rex , Allosaurus fragilis , Struthiomimus altus and Coelophysis bauri were

(A) Coelophysis bauri ; (B) Struthiomimus altus ; (C) Allosaurus fragilis ; (D) Baryonyx ( Suchomimus ) tenerensis ; (E) Spinosaurus aegyptiacus ; (F) Tyrannosaurus rex . Animals
Detailedview of the Spinosaurus “sail” andits associated neural spines
Three-dimensional alligator (Alligator mississippiensis ) model
(A) Spinosaurus aegyptiacus ; (B) Baryonyx ( Suchomimus ) tenerensis . Determination
(A) Coelophysis bauri ; (B) Struthiomimus altus ; (C) Allosaurus fragilis ; (D) Tyrannosaurus rex . See
AlternateSpinosaurus axial
A.f – Allosaurus fragilis , B.t – Baryonyx ( Suchomimus ) tenerensis , C.b – Coelophysis bauri , S.a – Struthiomimus altus , S.ae – Spinosaurus aegyptiacus , T.r – Tyrannosaurus rex .
Hatcher JG. 1901. Diplodocus Marsh, its osteology, taxonomy, and probable habits, with a restoration of the skeleton. Memoirs of the Carnegie Museum 1:1-64.


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 BUOYANCY, BALANCE AND STABILITY CHALLENGE TO THE HYPOTHESIS OF A SEMI-AQUATIC SPINOSAURUS STROMER, 1915 (DINOSAURIA: THEROPODA)
Review round: 1
Reviewer: 2

Output:
Basic reporting: Important references are missing, and the background provided is incomplete. Major problems are listed below.

- Important and highly relevant research is not cited and/or discussed - a major problem with this manuscript is that the author does not (or not sufficiently) address several very important issues, including 1) highly unusual adaptations in Spinosaurus used as evidence for a more aquatic lifestyle (e.g., bone histology results (higher bone compactness than Alligator); peculiar morphology of the pes; extremely retracted position of nares – see for example Ibrahim et al. 2014), 2) oxygen isotope analyses strongly suggesting a semiaquatic lifestyle (see for example Amiot et al. 2010), and 3) paleoecological aspects (e.g., presence of abundant giant fishes; very few remains of plant-eating dinosaurs in the Kem Kem and other equivalent sequences in North Africa; seemingly optimal conditions for large, fish-eating tetrapods and fish-based food webs – see for example Läng et al. 2013, Benyoucef et al. 2015).

- The content and narrative of the MS suggests that this is a critique of a “diving Spinosaurus” proposed by Ibrahim et al. 2014. A reading of Ibrahim et al. (2014), however, shows that these authors merely argue for semiaquatic habits, diving is not mentioned. They state, regarding the neck of Spinosaurus: “The horizontal cervicodorsal hinge created by these broad centra would facilitate dorsoventral excursion of the distal two thirds of the neck and skull in the pursuit of prey underwater”. This would be in agreement with the “floating Spinosaurus” presented here, so it is unclear why this MS is presented as a “critique” of the 2014 paper. Maybe the author is critiquing other papers relating to this dinosaur? Biophysicist Gimsa et al (2016), for example, specifically discuss the sail use and diving abilities of Spinosaurus.

- Page 9, line 76: Again, semiaquatic habits for spinosaurids have been proposed well before the “radical” 2014 paper by Ibrahim et al. For example, Amiot et al. (2010) have used detailed oxygen isotope analyses to come to the same conclusion. These other papers and lines of evidence definitely have to be thoroughly addressed here.

- Page 17, line 262: This claim appears to be inaccurate. According to Ibrahim et al (2014) the neotype skeleton includes at least some associated dorsal elements (vertebrae, spines).

Page 19, line 287: Again, this seems to contradict the published record. Ibrahim et al (2014) list at least one very large forelimb element (manual phalanx) associated with the axial and appendicular skeleton.

A few comments on wording, references etc.:

- Page 7, line 52: “Based on a skeletal reconstruction derived from several, isolated, partial specimens of the Late Cretaceous dinosaur Spinosaurus aegyptiacus,”.  This statement lacks precision. According to Ibrahim et al. (2014) the reconstruction is based on one partial, associated skeleton + isolated specimens from other localities. The current wording is confusing.

- Page 9, line 91: Make sure to order references chronologically here.

- Page 18, line 278: This should read “the lightest animal”

- Page 19, line 307: Reword this sentence.
Experimental design: The author might want to provide more details on his reconstruction of external and internal soft tissues for Spinosaurus which appears to differ from other theropods in many features, including the (presumably) very small fleshy nares for an animal this size. Why, for example, was the size and distribution of air sacs assumed to be the same for all the theropods?

The theropod models used here all seem to be based on the same parameters (in density for example). This approach does not seem to take into account that Spinosaurus had denser bone than other theropods (see Ibrahim et al. 2014). Clearly, the models need to take into account such factors. Again, the author might want to examine the remains of Spinosaurus in person to ascertain bone density in different parts of the skeleton.
See for example this paragraph from Coughlin and Fish (2009), Journal of Mammalogy: “Increasing body density by increased deposition of compact bone in the appendicular skeleton has been cited as a means that semiaquatic mammals can use to increase their specific density to overcome buoyancy (Fish and Stein 1991; Wall 1983). Osteosclerosis is an increase in bone density by the replacement of cancellous bone with compact bone or by increasing cortical bone thickness at the expense of the medullary cavity (Domning and de Buffrénil 1991; Thewissen et al. 2007; Wall 1983). Osteosclerosis is a common adaptation in semiaquatic and aquatic mammals for buoyancy control (Domning and de Buffrénil 1991; Fish and Stein 1991; Gray et al. 2007; Wall 1983). Additional bone density is achieved by tightly packing cancellous bone into the medullary cavity, as occurs in H. amphibius (Wall 1983).”

It would be helpful and important to compare Spinosaurus to a hippo, a semiaquatic animal with high-density bone that is considered an excellent diver (Coughlin and Fish 2009). How does the buoyancy of a hippo compare?

Other problems with the models used:

- Page 15, line 218: The proportions (and, possibly, density) of Spinosaurus appear to be very different from those of pigeons and ostriches. The author might want to explain how those differences have been taken into account.

- Table 2: The body length estimate for Spinosaurus (16 m) provided in the MS seems to be longer than the ~15 m estimate by Ibrahim et al (2014).

A few more issues:

- Page 8, line 56: Contrary to one or two usages of the term in the literature, the Kem Kem sequence has never been defined as a formation. The author might want to use the term “Kem Kem beds” instead. See also Cavin et al. (2010) for an alternative interpretation of the sequence.

- Page 8, line 57: “This interpretation of an extinct theropod as being semi-aquatic was entirely novel, and generated much media attention (eg. Tarlach, 2014; Coghlan, 2014).” Media attention is probably not a relevant factor in this technical publication and should not be mentioned in the context of scientific issues.
Validity of the findings: In addition to methodological issues and missing background infromation, there are also some other problems with the conclusions:

- That theropods could float (and swim) is expected and consistent with previous work and ichnofossils. Unfortunately the author does not shed light on the reasons why Spinosaurus shows so many anatomical features typically associated with increased semiaquatic, or aquatic, lifestyles in other vertebrates. More importantly, if Spinosaurus is “like Baryonyx”, why is its skull and postcranial anatomy so different and – according to many researchers – consistent with increasingly aquatic habits? These major issues, which are at the heart of recent reconstructions, are not sufficiently addressed.

- Page 20, final part of conclusion: “Lastly, the new reconstruction of Spinosaurus is based on a composition of remains from multiple individuals of varying sizes and proportions that come from different locations, and were scaled to match the presumed proportions of a single individual. This does not seem like a good platform for building hypotheses about what this animal was like as a once living organism.”

But is this not what paleontologists have to work with much of the time? Indeed, the author (Henderson, 2010) has used the same approach when reconstructing the weight and flight abilities of the giant pterosaur Quetzalcoatlus, a taxon known from (often very) incomplete remains representing multiple individuals of varying sizes, from different locations in Texas’ Big Bend National Park (Javelina Formation), and frequently scaled to match the presumed proportions of a single individual (see Henderson 2010)…
Additional comments: The author attempts to shed light on the buoyancy and balance of a bizarre predatory dinosaur, Spinosaurus aegyptiacus. This is an interesting modeling approach to a potentially unique animal and includes interesting aspects, such as a reassessment of the center of mass. Unfortunately the manuscript, in its current form, is lacking in a number of very important areas and will require substantial revision before it can be considered for publication. For details on how best to improve different aspects of the manuscripts see comments and references in the relevant review sections.

It is also not clear from the manuscript whether the author examined the Spinosaurus material in person. Presumably, this would be very important to ensure that the model is as accurate as possible (e.g., first-hand study of spines and long bones, establishing bone density values for different parts of the skeleton, etc).


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 BUOYANCY, BALANCE AND STABILITY CHALLENGE TO THE HYPOTHESIS OF A SEMI-AQUATIC SPINOSAURUS STROMER, 1915 (DINOSAURIA: THEROPODA)
Review round: 1
Reviewer: 3

Output:
Basic reporting: Clear English is used throughout, bar the following minor issues:
-	Line 41: “e.g. examples” I think reads better than “examples, etc.”
-	Line 149: Is the comma between ‘large’ and ‘reptile’ a typo?
-	Line 211: ‘Contrary to Ibrahim et al. (2014) that the centre’, it seems like a word may be missing here (something like ‘Contrary to Ibrahim et al.’s (2014) statement’?)

Sufficient literature references and context are provided.

The article structure is logical and reads well. Raw data is shared, but inclusion of the polygon meshes used to reconstruct body mass properties would be nice for repeatability / investigation using reconstruction techniques other than the authors outline-based ‘mathematical slicing’.

The article is appropriately self-contained, given that the method has been well-explained elsewhere in previous papers.
Experimental design: This is original primary research and by my judgement it fits within the aims and scopes of the journal.

The research question is well-defined, relevant and meaningful to the field of dinosaur behaviour reconstruction, both in terms of its results and its methodology.

The investigation is sufficiently rigorous and is at the upper end of the technical methods for the field. Ethics concerns are not applicable.

The methods are well described and replicable, albeit only with reference to the authors earlier works. I do not consider the latter a problem.
Validity of the findings: This is essentially ‘meaningful replication’, in that it is an attempt to replicate the centre of mass estimated of Ibrahim et al.’s 2014 study, but using an explicitly explained (albeit in earlier work) and well-validated method, rather than the unexplained method of Ibrahim et al. As Ibrahim et al. made what could be considered extraordinary claims (a quadrupedal, habitually aquatic non-avian theropod), but do not state their method fully, an attempt to replicate their findings is fully justified. In addition, the centre-of-buoyancy calculations are fascinating in themselves, and definitely add meaningful data to the field.

The robusticity of the data is I think sufficient. The author goes to some lengths to vary his assumptions in order to disprove his main findings. However, the validation of his methodology would be (to my mind) more convincing if an aquatic theropod (a duck maybe?) were included along with the alligator model. This also pertains to some of the statements made in defence of a non-aquatic Spinosaurus (see general comments below). The descriptive statistics used to summarise the data are simple but entirely appropriate for the sample.

The conclusions of the study are well-considered and well-stated (but see general comments below), and linked well to the primary research question(s) of the paper.

Speculation is minimal (although I have some suggestions in that regard, see general comments) and identified where present.
Additional comments: I congratulate the author on a well-conceived and well-executed study that addresses a pertinent question in dinosaur behavioural research, reported with a clear, concise and very readable manuscript. I do however have some suggestions that I think may improve the study. Firstly, there is no mention made of diving birds – how does their density / pneumatisation compare to that reconstructed here for a typical non-avian theropod? How does this affect their buoyancy both with/without the lungs collapsed? I would be interested to see how a model based on a living aquatic, predatory theropod would compare to the model of Spinosaurus in terms of unsinkability. I would be interested to see how much the density of the Spinosaurus model would have to be increased by in order for it to sink. If given an alligator-style, unpneumatised chest, how would this affect your results? Similarly, while the authors sensitivity analysis is satisfying, I would be interested to hear the author speculate as to what model parameters would be necessary to match the results of Ibrahim et al. (2014).

Also, several of the criteria used as evidence against aquatic behaviour (tightly-fitted acetabulum, stiff abdomen) also exist in swimming birds. The argument against swimming using limb-reduction and streamlining is, also, based on the style of axial propulsion seen in modern crocodilians, and so it seems somewhat tautological so use this for argument an animal like Spinosaurus that is already stated unlikely to be capable of significant lateral body-and-tail flexion. What about paddling? I think a sentence or two addressing this would benefit the article.

Finally, I think Figure 7 may be unnecessary. The summary statistics it represents can be (and are) adequately communicated in the text.

I enjoyed reading this article and look forward to seeing it published. If the author wishes to discuss any of the points raised in this review they are welcome to email me on vallen@rvc.ac.uk.

Dr. Vivian Allen


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 BUOYANCY, BALANCE AND STABILITY CHALLENGE TO THE HYPOTHESIS OF A SEMI-AQUATIC SPINOSAURUS STROMER, 1915 (DINOSAURIA: THEROPODA)
Review round: 2
Reviewer: 1

Output:
Basic reporting: This is a re-review and my previous comments stand.
Experimental design: The author has partly taken on board my comments about transverse stability, but addressed them in a convoluted and unnecessarily complex fashion, which in fact does not quite answer the question. The results are for idealised 2 dimensional "animals" and thus produce results that could questioned in relation to the actual morphology.

In fact, I think the authors conclusions about the instability of the spinosaurids will not change if the whole body stability is calculated, and that actually seems to me to be a very important argument against fully aquatic ability. As such, the paper is OK as it stands, but why not include a more robust stability estimation? For this reason, I think a final revision is required to polish an otherwise fine piece of work.

It really is quite simple to do the calculations for the complete animal, as I will set out below in the comments to the author.
Validity of the findings: The author has addressed my concerns about sensitivity, so no further comment (but see above).
Additional comments: Don, the calculation of the transverse stability of a floating body is relatively straightforward, and gives the answer for the whole body, as distinct from an idealised 2D cross section as in your additions to the paper. The way it works is set out in naval architecture text books, but in brief:

First you calculate the metacentric height, conventionally BM, the distance between the centre of buoyancy and the "metacentre", the point on the centreline where the line of action of the vertical buoyancy force crosses.

BM is simply the second moment of area of the waterplane (I) divided by the displaced volume (V). So:

BM=I/V.

A body is stable if the distance from the centre of gravity to M (GM) is positive.

I have done quick calculations for the alligator (using screen grabs from your paper, so accuracy may not be great) and can send you the spreadsheet if it helps.


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 BUOYANCY, BALANCE AND STABILITY CHALLENGE TO THE HYPOTHESIS OF A SEMI-AQUATIC SPINOSAURUS STROMER, 1915 (DINOSAURIA: THEROPODA)
Review round: 2
Reviewer: 2

Output:
Basic reporting: The background provided must be improved.

Let me use an example I have already mentioned (but these comments have not really been addressed):

“The radical claim by Ibrahim et al. (2014) of a semi-aquatic theropod dinosaur inspired further investigation of the aquatic potential of Spinosaurus,”

As mentioned in the previous review, why under-cite here? There are a number of papers dealing with this topic, in particular Amiot et al’s landmark work using oxygen isotopes. After all, the title of their paper is "Oxygen isotope evidence for semi-aquatic habits among spinosaurid theropods". That is a very clear statement, right in the title.

The author also needs to address (or at the very least mention) the important and well-documented conclusions these authors reached: "On the basis of the oxygen isotopic composition of their phosphatic remains compared with those of coexisting terrestrial theropod dinosaurs and semiaquatic crocodilians and turtles, we conclude that spinosaurs had semiaquatic lifestyles, i.e., they spent a large part of their daily time in water, like extant crocodilians or hippopotamuses."

Why is this key paper (and others published on potentially semiaquatic dinosaurs over the last few years), published in the high-impact journal Geology, largely ignored in the first few pages?

The author (at the end of the MS) claims that Amiot et al infer fish-eating and not much else. Again, this is clearly not consistent with what the authors actually concluded (see above).

PeerJ guidelines clearly state that literature should be cited appropriately and enough background should be provided. This is not always the case here.

Another example that has not been addressed at all:

“In particular, the hind limbs of the new restoration, although from a single
individual, were not associated with the dorsal axial skeleton which forms a substantial part of the body.”

This seems to contradict Ibrahim et al 2014. Unless the author had access to unpublished data from these authors suggesting otherwise, this statement needs to be changed.

“Again, the forelimbs were not found in association with the hindlimbs , are composites derived from isolated remains, and not associated with the portions of the dorsal axial skeleton.”

Again, this contradicts the paper cited, which states that at least two forelimb elements were associated with the axial elements. If the author did have access to unpublished data contradicting this, it needs to be mentioned here (at the very least a "pers. com.").

These issues must be addressed, considering that they simply relate to accurate referencing and reporting of previously published work.
Experimental design: The author has addressed some of the issues mentioned (though not all - see previous round of comments).

The research questions are well-defined. The methods are mostly described in sufficient detail, and overall this is quite an impressive piece of work, but more information should be provided on the caveats and limitations.

Some details should be explained a little further. Example:

 “The sail was assumed to be covered with skin to a depth of 1 cm on both sides”

Not sure where some of these estimates come from - some background would be helpful.

“It was suggested by a reviewer that a test of the software and methods should also be 162 done with a living, aquatic, predatory theropod, ie. a diving bird, to see how it would compare to Spinosaurus. This was done with a model of an emperor penguin (Aptenodytes forsteri Gray 164)."

This is very helpful and really improved this section of the manuscript.

It is important to note somewhere that the work presented here is not based on first-hand study of the fossil material.
Validity of the findings: Not addressing some previously published results (e.g. Amiot et al.), or limitations of the approach taken here, or implying that this paper trumps all other lines of evidence, weakens this contribution.

A more nuanced, balanced reporting of the findings would considerably improve this manuscript.
Additional comments: This is certainly an improved version, but a number of issues need to be addressed before this contribution is consistent with PeerJ guidelines (see detailed comments above). The author is a world-leading expert in his field. Unfortunately, unlike comparable papers published in the past (e.g. Henderson and Naish 2010; Henderson 2006), this particular manuscript is still lacking important context (see above) and a more detailed account of the limitations of the approaches taken here.

I am recommending "minor revisions", even though the list of issues that have not been fully addressed is relatively long (see also first review). At the very least this contribution needs:

1) a more complete and detailed background section, mentioning previous research on spinosaurid lifestyles and addressing other lines of evidence more fully (this is particularly true for the crucial - but under-cited - Amiot et al study, but also other papers, e.g. Gimsa et al. 2016, Vullo et al. 2016). More context on other papers relating to potentially semiaquatic dinosaurs (e.g. Ford and Martin 2010) would also be helpful.

2) a more detailed account of the limitations of this study (this includes methodological weaknesses , as well as issues of data quality (e.g., original fossil material was not examined to build the model)).

3) a possible alternative explanation as to why Spinosaurus shows so many anatomical features typically associated with increased semiaquatic, or aquatic, lifestyles in other vertebrates. Simply dismissing them (as is somewhat implied in the MS) is probably not the right approach. Again, a more nuanced discussion of findings would be very helpful here (e.g. can all those different results be reconciled in some way? If not, what might that mean?). Also, as mentioned in my previous review, if Spinosaurus is “like Baryonyx”, why is its skull and postcranial anatomy so different?

A few questions re: the rebuttal file:

"Comments “Page17”, “Page19”: this is just a petty, defensive detail. No action taken."

Please specify which comments this refers to. This doesn’t seem to match the comments on these pages from my review -

"Comment “Page 8, line 57”: Why not mention the widespread public interest in the new interpretation of Spinosaurus? Does it not indicate the appeal of the subject, demonstrate the engagement of the public with the science, and show why it is worth doing the science?"

Sure, but not in a paper on a completely different subject, i.e. this is not a paper on the public understanding of science or the importance of palaeontological research. I am not sure how exactly this relates to the subject matter of this technical paper.

Finally, the paper ends on the following note:

- Page 20, final part of conclusion: “Lastly, the new reconstruction of Spinosaurus is based on a composition of remains from multiple individuals of varying sizes and proportions that come from different locations, and were scaled to match the presumed proportions of a single individual. This does not seem like a good platform for building hypotheses about what this animal was like as a once living organism.”

This sounds like a rather sweeping criticism of much of palaeontological research (many, many dinosaur palaeontology papers would fall in that category). Is this not what paleontologists have to work with much of the time? Does the building of hypotheses, even when they are built on incomplete skeletons, advance the science of palaeontology? As mentioned before, the author (Henderson, 2010) has used the same approach when reconstructing the weight and flight abilities of the giant pterosaur Quetzalcoatlus, a taxon known from (often very) incomplete remains representing multiple individuals of varying sizes, from different locations in Texas’ Big Bend National Park (Javelina Formation), and frequently scaled to match the presumed proportions of a single individual (see Henderson 2010).

I am not sure the paper needs to end on such a note, but since this is not a technical comment, this is up to the author.


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 BUOYANCY, BALANCE AND STABILITY CHALLENGE TO THE HYPOTHESIS OF A SEMI-AQUATIC SPINOSAURUS STROMER, 1915 (DINOSAURIA: THEROPODA)
Review round: 2
Reviewer: 3

Output:
Basic reporting: As previous review
Experimental design: As previous review
Validity of the findings: As previous review
Additional comments: I commend the author on this edited and expanded study. The extra inclusions I think work really well! All of my comments have either been satisfactorily addressed, or were merely a difference in opinion regarding reporting style (i.e. inclusion or not of fig. 7) and so are entirely at the authors discretion to follow. I look forward to seeing this work published.


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 BUOYANCY, BALANCE AND STABILITY CHALLENGE TO THE HYPOTHESIS OF A SEMI-AQUATIC SPINOSAURUS STROMER, 1915 (DINOSAURIA: THEROPODA)
Review round: 3
Reviewer: 1

Output:
Basic reporting: As before
Experimental design: The author has made an attempt to use the conventional engineering approach to stability calculation, but I am afraid that I still have reservations and comments. I am sorry if this appears pedantic, but I do believe that there are simple ways in which the stability differences between the different the animals can be convincingly demonstrated.

As I have typed my comments as a separate file, please see attached.
Validity of the findings: As before
Additional comments: Please see attached.


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 BUOYANCY, BALANCE AND STABILITY CHALLENGE TO THE HYPOTHESIS OF A SEMI-AQUATIC SPINOSAURUS STROMER, 1915 (DINOSAURIA: THEROPODA)
Review round: 3
Reviewer: 2

Output:
Basic reporting: MS looks much better. The model still seems to be lacking a few key features (e.g., dense bone in other parts of the skeleton - not just the hind limbs), but these potential weaknesses can be explained in the text.

As already discussed previously, only Gimsa et al. appear to argue in favor of diving and "fish-like" pursuit of prey under water. The starting point and some of the narratives of this MS are, in some ways, based on a strawman "opponent". Most authors have simply advocated "semiaquatic habits/lifestyle", which, according to most definitions, does not necessarily imply deep water hunting/diving etc. Shallow water hunting is not an option that has been ruled out by other authors.

In other words, most of the results presented here do not appear to really contradict previous papers (Gimsa et al being an exception). The MS should definitely reflect this - in its current form, it still doesn't.
Experimental design: The model still seems to be lacking a few key features (e.g., dense bone in other parts of the skeleton - not just the hind limbs), but these potential weaknesses can be explained in the text.

Without a detailed osteohistological analysis of the partial skeleton, the model presented here remains quite speculative (e.g. distribution of dense bone etc.). This should be reflected in the text.
Validity of the findings: The data is not as robust as it could be (see above), and this needs to be reflected in the text.
Additional comments: The unique (amongst dinosaurs) position of the fossa for the fleshy nostril should probably be discussed in more detail. Why would a more–or–less terrestrial animal have such a unique adaptation?

Ibrahim et al. list “Short centra and reduced neural arch articulations” in the tail, features that differ from most other theropods and would presumably have increased flexibility. This should be addressed in a relevant section.

Line 73 – See previous comments. “Media attention” has no relevance to the topic discussed here.

Line 162 – “Lacking evidence to the contrary” is not a strong argument in favor of the selected thickness…

Line 275 – is this Wikipedia reference reliable?

Line 314 – Maybe better to include this in the figure.

Line 329 – Why “caimans” and not “caiman”?

Line 379 – This doesn’t make sense. Why is solid bone assumed to be restricted to just the hind limbs? Many extant aquatic and semi-aquatic vertebrates also have very dense ribs (see manatees for example) etc. – why should Spinosaurus be any different? And what about the dense spines?

Line 391 – There is a word missing here.

Line 529-533 – see previous rounds of 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 BUOYANCY, BALANCE AND STABILITY CHALLENGE TO THE HYPOTHESIS OF A SEMI-AQUATIC SPINOSAURUS STROMER, 1915 (DINOSAURIA: THEROPODA)
Review round: 4
Reviewer: 1

Output:
Basic reporting: This is my third review of the paper, so most comments as before.
Experimental design: The analysis of lateral stability is now acceptable.
Validity of the findings: As before
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 BUOYANCY, BALANCE AND STABILITY CHALLENGE TO THE HYPOTHESIS OF A SEMI-AQUATIC SPINOSAURUS STROMER, 1915 (DINOSAURIA: THEROPODA)
Review round: 4
Reviewer: 2

Output:
Basic reporting: The paper is well written.

The literature cited is sufficient and a broad background is presented.

The raw data shared are sufficient.

The paper is relevant
Experimental design: The dataset used for testing the hypothesis is adequate and impressive. The data are novel and the new quantification for swimming modes are excellent. However, I have some doubts regarding the material and methods. The model of Spinosaurus is slightly different from the one previously published, and it is not clear from the text what changed and why. Several tests are giving different results from previous papers, but it is not explained in which way the analyses reported in Henderson are different from the previous ones. Osteosclerosis in Spinosaurus is only limited to the appendicular skeleton in this study, even though it was found in the dorsal spines as well. Moreover, osteosclerosis is not reported in some tests. In the end, extant taxa should be used for every test in the paper, in order to validate the results and the interpretation of the analyses.
Validity of the findings: I would like to see more tests to validate the results already obtained in the paper
Additional comments: The paper is relevant and exciting, but needs more tests to back up the claims


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: ALU HYPERMETHYLATION AND HIGH OXIDATIVE STRESS IN PATIENTS WITH MUSCULOSKELETAL TUMORS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The English is not of a standard that is acceptable for publication. There are some statements that are frankly incorrect e.g. osteogenic and chondrogenis sarcoma affect mainly children. Osteosarcoma affects mainly children but chondrosarcoma affects mainly adults. The statement that patients with MS tumor under the age of 20 all being dead is completely inaccurate.
The data is incomplete- there are about 40 patients assessed but there is no information regarding the type of tumours they had or whether they received any other treatment such as chemotherapy.
Experimental design: The research question is clear i.e. whether Alu methylation correlates with outcomes but the importance of this has been overstated. Other blood tests such as CRP correlate with survival in bone sarcoma and can be carried out cheaply.
The methodology does not contain enough information to allow repetition. There is no description how the tissue lysates were derived or how the plasma from blood samples was obtained.
Validity of the findings: The main flaw of this paper is the Alu gel which shows some bands that do not vary between the conditions. The authors then extrapolate these bands to suggest that there is a difference. This is misleading- the bands can only be semi-quantified at best, but the authors do not provide any raw data to demonstrate how they have performed their quantification. The data is NOT robust and is essentially meaningless.
Additional comments: This paper does not contribute anything of value. If experiments are done on tissues and blood, it should at least be explained exactly what tumour sub-types were studied. The methodology is poor and the interpretation of the data is overblown.


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: ALU HYPERMETHYLATION AND HIGH OXIDATIVE STRESS IN PATIENTS WITH MUSCULOSKELETAL TUMORS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The structure of the manuscript is clear and logical, with figures that clearly illustrate the main findings. However, there are some issues with phrasing and the language throughout the manuscript. It would benefit from careful proof-reading and editing, perhaps with assistance from a native English speaker if possible.
Experimental design: The research question is well defined and addressed. However, several aspects of the methods need to be clarified to ensure the work was performed to suitably high standards. COBRA is also not a sensitive technique, and the Alu sequences interrogated by the assay need to be confirmed.
Validity of the findings: The data appears to be robust and appropriately analysed, and the conclusions are supported by the findings.
Additional comments: The work is interesting and suggests that Alu methylation should be explored further in MS tumours, both in terms of mechanistic studies and examination of its potential as a diagnostic/prognostic biomarker. However, some issues in the manuscript need to be addressed.

Major comments
1. Which Alu elements in the genome are being interrogated by the COBRA assay? Alu elements can be categorised by their evolutionary origin, with the widely used pyrosequencing assay specifically interrogating Alu Sx sequences in the human genome. It is known that these subfamilies display differential methylation, such as in response to environmental pollutants (Byun et al, 2013, Part Fibre Toxicol 10:28). Furthermore, only AluY sequences are believed to have retained the ability to retrotranspose within the genome. It is therefore important to appreciate which subfamilies may be analysed by this assay.

2. As noted by the authors, most studies have reported hypomethylation of Alu elements in cancer, which may lead to genomic instability. In the Discussion section the authors should address the possible implications of Alu hypermethylation and how it may be implicated in carcinogenesis.

3. Were Alu methylation and 8-OHdG levels in tumours examined in relation to tumour stage or grade?

4. The authors commented on the heterogenous nature of the MS tumours. A description of the tumour types and numbers of patients should be provided in the Methods section (Line 119 onwards). Furthermore, were differences in Alu methylation and 8-OHdG levels examined between the different subtypes?

5. The analysis of the COBRA data is not well explained. The authors should modify the ‘Alu methylation analysis’ subsection of the Methods (Line 147) to provide a better description of how the results were interpreted, to enable the reader to more easily understand the work that was performed.

6. Where was the adjacent tissue taken from, i.e. what distance from the tumour? Was the tissue examined by a histopathologist to confirm the absence of malignant cells? These are important issues to clarify due to the possibility of field defects in the surrounding normal tissue.

7. Was a standard curve used for the ELISA measuring 8-OHdG levels? If so, this should be clarified in the Methods section (Line 164).

8. Was the analysis of 8-OHdG performed in plasma for both the 107 healthy controls and 40 patients (Line 222 and Figure 5B)? If so, the text should be modified to avoid referring to “tumors”, as this implies analysis of tumour tissue rather than plasma.

9. The AUC from the ROC analysis is reasonably promising and should form part of the discussion of the potential of Alu methylation as a blood-based biomarker of MS tumours (Lines 278-281).

10. The Conclusions paragraph (Line 310) should be re-written so that it does not simply repeat the findings once more.

11. In Figure 3, two outliers seem to have erroneously high methylation levels in leukocytes. Are the authors confident that the results for these two samples are accurate?

12. In the analysis of relative disease risk, why was the methylation data dichotomised by the median value (Line 214), rather than the threshold identified by ROC analysis (Line 208)? Furthermore, the sentence beginning “A high methylation” on Line 215 should be re-written to clarify the meaning.

Minor comments
Line 66: The sentence ending “usually dead” needs to be revised to clarify the meaning and to be more delicately phrased.
Line 95: The sentence beginning “Moreover, 8-OHdG can interfere” should be rewritten to something more specific, such as by describing how 8-OHdG could lead to base changes at CpG sites that eliminate the possibly of methylation.
Line 154: Here the authors state that the assay produces 6 bands, but later they describe the assay as producing 5. This should be corrected.
Line 166: The ELISA kit should be named.
Line 196: The mean/median methylation levels in tumours, adjacent tissue and blood samples should be written in the text, to help the reader understand the magnitude of the changes in methylation being reported.
Line 231: The opening paragraph of the Discussion uses the phrase “to the controls” or “than in the controls” a total of five times, which is too repetitive. These could be removed without affecting how the reader will interpret the paragraph.
Line 257: A reference for the pancreatic cancer study appears to be missing.
Line 258: “PMR” needs to be defined. What is it?
Line 264: The suggestion that the tumours have double stranded breaks that are easily methylated is speculative. Please rephrase this sentence to be more cautious.
Line 273: The sentence beginning “These findings” should be revised to be more cautious, as those results alone do not suggest that Alu hypomethylation leads to genomic instability.
Line 288: Again, more caution must be taken into the inferences made from results. There is nothing to suggest that 8-OHdG could remodel chromatin structure simply from those results.


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: DE NOVO OVIDUCT TRANSCRIPTOME OF THE MOOR FROG RANA ARVALIS: A QUEST FOR MATERNAL EFFECT CANDIDATE GENES
Review round: 1
Reviewer: 1

Output:
Basic reporting: In general, the quality of the writing and English is good and there is a sufficient amount of background material in the introduction as well as explanatory information in the materials and methods section. I note, though, that there are some sentence or grammar issues throughout – these aren’t grave but they are noticeable. For instance, on line 360 “high among individual polymorphism…is high” should have one fewer uses of “high”. The figures and tables are predominantly clear and easy to comprehend. Though in Figure 2C, there are a few issues with the species labeling. The second species is given only a common name (African clawed frog) whereas all other taxa are given their scientific names – this should be Xenopus laevis. Additionally, the 3rd to last species is labeled Aquarana catesbeiana but no such species exists. This references the American bullfrog (Rana catesbeiana), a congener of the focus species of this manuscript separated by ~40my. “Aquarana” refers to a subgeneric clade of eastern North American frogs but is not the genus of this species. The liver fluke Clonorchis sinensis is misspelled as “siensis”. Also, for Figure 5, is the Y-axis on a log scale? But generally, the goal of the paper is laid out well and the analyses and discussion are pertinent to the results.
Experimental design: I find this work to be well within the scope of the journal. It is clear what the authors set out to do, their methods are generally easy to follow, and most importantly the work was generally done in a suitable way to accomplish the intended goal. Any clarifications I need are outlined below in the general comments.
Validity of the findings: My reading of this work as that the authors have done a sufficient job of producing, refining, and analyzing the data to identify candidate loci that might be involved with maternal effects of acid tolerance via manipulation the oocyte jelly coat.
Additional comments: •	In your abstract and elsewhere you note that egg jelly coats are an important, often neglected source of maternal effects. I certainly agree. But perhaps it would be best to note that this is predominantly for external fertilizing species like most anamniotes (fishes and amphibians) and wouldn’t apply to most other tetrapods?
•	I like the authors’ use of a gradient approach here, using three populations varying in acid tolerance as well as two individuals within each population varying in acid tolerance. I initially liked the idea of the unovulated control female but not sure she actually constitutes a real control without similar individuals in all three populations. Data from this individual are generally downplayed throughout this manuscript too and in large part that makes sense because this individual is really only expected to differ in transcript discovery and transcription levels but not architectural (i.e., coding) differences. However, given this unovulated individual is neglected from Figure 7, the key figure on transcription differences, perhaps remove most of the reference to this individual in the methods, results, and discussion and just point to her transcript information in the supplement and the eventual publication of her data on online databases?
•	I wonder with the number of unigenes presented for three parasites (the Clonorchis and two Schistosoma), whether these are true R. arvalis transcripts or whether the authors acquired RNA from parasites. In Molecular Phylogenetics and Evolution, Juan Santos and colleagues recently mined transcriptome data to look at endoparasite diversity in the guts of Dendrobatid frogs (Diversity within diversity: Parasite species richness in poison frogs assessed by transcriptomics). I don’t know the answer, but perhaps the authors can discuss a bit whether these RNA seq data are the result of sequence similarity to parasite transcripts or whether these are actual parasitization of the reproductive tract. The authors touch on this very briefly (on line 323) but it’s probably worth discussing more given how prevalent it was in your results.
•	If the authors were predicting amino acid sequences, could they also discuss whether these differences represent synonymous mutations or not? I think this would be relevant if we are talking about possible genomic architectural differences underlying “maternal effects”
•	The authors mention a couple of times that only 2 amphibian genomes are available. This isn’t true. The bullfrog (Rana catesbeiana; draft genome in Hammond et al. 2017, Nature Communications), the Iberian ribbed newt (Pleurodeles waltl; genome in Elewa et al. 2017, Nature Communications), and the axolotl (Ambystoma mexicanum; in Nowoshilow et al. 2018, Nature).
•	Out of curiosity, were there any hits to transcriptomic resources developed for the green frog (Rana clamitans) and chorus frog (Pseudacris regilla) published in Robertson and Cornman (2014, Molecular Ecology)? I imagine they would have showed up in your discussion if this was relevant but green frogs are relatively closely related to Rana arvalis so I thought it would be worth checking
•	You mention a few times that most of the unigenes couldn’t be annotated with existing databases because a lack of genomics resources. But it also isn’t surprising given the authors only used a single tissue type (oviduct) and given most studies focus on other tissues (brain, heart, liver, kidney, skeletal muscle). The authors had a very good reason to target oviduct, but I’m not really surprised most of these genes weren’t annotatable.
•	I think the authors need to spend some time defining their interpretation of genetic / genomic architecture. This term typically refers to coding differences and is relatable to the microsatellite repeat and SNP loci identified by the authors. However, general differences in the number of transcripts don’t relate to genomic architecture. These might instead relate to regulatory differences that could even be intronic and not looked at in this study. Maternal effects are generally considered a plastic response and therefore the authors can’t really get at that here given tissues were harvested from animals housed in similar conditions. What the transcription and architectural data show is that are innate differences both in sequences of functional regions of the genome as well as transcriptional differences among populations independent of current conditions, although transcriptional differences may also affected by the conditions experienced when these females were tadpoles. Basically, I think the authors need to be a bit more careful in discussing the material throughout this manuscript. As it reads now, it suggests that transcriptional and coding differences found here are related to maternal effects. What you’ve really identified are candidate loci that might be innately or plastically (or both) influence acid tolerance in different population. I believe the authors mean to say this, and the title does indeed signify a quest for candidate loci, but the manuscript reads as if it is suggesting the differences detected here are driving maternal effects.
•	Lines 278-286 discuss the number of transcriptional differences between populations. Because these are wild-caught adults, it is unclear whether differences are innate, genetic differences or whether they are plastic responses to tadpole rearing environment. Regardless, these are interesting results. The methods for these results aren’t particularly clear. Perhaps the authors could elaborate any statistical analyses done for this result and maybe provide a figure? Additionally, given the authors are able to rank each individual frog’s degree of acid tolerance from work elsewhere, perhaps the authors could use some regression analysis to test whether a frog’s acid tolerance is related to transcriptional activity at all loci or particular loci to draw some additional inference?
•	Additionally, to what degree are various SSRs and SNPs related to each population’s degree of acidity? I fully recognize that the authors only analyzed 3 populations with only 2 individuals per population. But it would be tantalizing if there were loci where SSRs or SNPS segregated by the degree of acidity. This might possibly make these loci more suitable candidates for future functional / maternal effects work given you identified far more loci than you can possible assess in future analyses anyways.


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: DE NOVO OVIDUCT TRANSCRIPTOME OF THE MOOR FROG RANA ARVALIS: A QUEST FOR MATERNAL EFFECT CANDIDATE GENES
Review round: 1
Reviewer: 2

Output:
Basic reporting: This manuscript is engaging and interesting to read and is written well.

With respect to the samples – ponds and individual animals, the method need to be more clear. Please be careful to define exactly what you mean by descriptive words eg. sensitive, mature.

Line 112 – maybe use as second set of brackets around the abbreviation for the study sites so it is clear that they are abbreviations eg. (Tottajarn [T].
Line 131 – this is not completely clear what you mean.  Are these the most acid sensitive based on where there were captured, or the most sensitive from the ones captured at that site?
Line 232 – please define immature vs mature in the methods. Do you mean the ovulated vs not ovulated (line 133)? If so, immature/mature probably aren’t appropriate words.
Experimental design: Why is the pH in these ponds so different? Is it natural or is it from something else? Whatever is altering the pH in these ponds might alter the transcriptome of the frogs, it might not necessarily be the pH itself.

The hypothesis of this manuscript is that the frogs may alter their egg  coat composition in order to cope with the changes in the environment seen at the 3 pond sites. Is there any evidence for this? Have the proteins contained within the egg jelly of this species been identified – how do the proteins identified relate to the genes you have identified? Can the egg coats themselves from the 3 ponds be analyzed?

Line 116 – is it really possible to say that S is the most acid sensitive and T is the most acid tolerant? Do you have breeding information from these sites – are these frogs able to breed as effectively in all sites or are they less able to breed in one site?

Line 134 – are there different regions within the frog oviduct as there are in mammalian, reptilian and avian oviducts? If there are, then differences in RNA transcription in specific regions of the oviduct may be missed by this method.
Validity of the findings: Overall, there is a lot of data presented in this manuscript, but due to the difficulties associated with working with this species, not a lot can be concluded at this point.

However the data presented is robust and appears well controlled (except for experimental questions above).

The questions being asked are interesting and worthy of continued research.
Additional comments: Thank you for the opportunity to review this interesting manuscript.