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: RELATIONSHIPS BETWEEN CONSUMPTION OF ULTRA-PROCESSED FOODS, GESTATIONAL WEIGHT GAIN AND NEONATAL OUTCOMES IN A SAMPLE OF US PREGNANT WOMEN
Review round: 1
Reviewer: 1

Output:
Basic reporting: The present study is a longitudinal study aimed to evaluate the relationship between percent of energy intake from ultra-processed foods during pregnancy and maternal and neonatal outcomes related to weight gain and body composition.
The article adheres to PeerJ policies in terms of structure, and is written in a clear language providing eloquent explanations.
The introduction section is clear and outlines basic principles about dietary intake during pregnancy that aid in understanding the study design and results sections.  However there are certain aspects not discussed in the introduction – for example the outcomes of previously published articles using the same data, or the use of the Diet History questionnaire II. As a result these are discussed in the methods section which becomes over-detailed (see examples at “Experimental design” below).

Specific comments regarding introduction:
•	In lines 33-34 “… has been recommended” – a specific reference should be related to these recommendations. If the authors are referring to recommendations by Imhoff-Kunsch & Martorell 2012 then the location of the reference (now appears as if relates only to previous sentence) should be changed accordingly.
•	Line 64 – “critical” is a strong word to describe the role of UPF consumption in maternal and neonatal health. Maybe “important” or “of importance” or any other choice of words should be considered.

Figures and tables are relevant to the content of the article, and are adequately labeled. However, sometimes the text lacks adequate referral to the tables. The first time that tables 3+4 are presented in the text (line 194) there should be a clear referral as to what information the table holds (like previously reported for table 1+2), so that the even a reader that does not want to approach the table at the same time will understand it’s value. When citing data from table 5 in lines 220-221 it is advisable to include p-values in the text since these are the major outcomes of the study (same as should be mentioned for all outcomes in the text).
Specific comments –
•	The use of an asterisk in the tables to emphesize p-value<0.005 is confusing in tables 3&4 when it is also used in the first column (“for PEI-UPF * Age” etc.). Alternative symbol can be used or significant p-values can be bold text.
Experimental design: The study design relies on data collected for previously published studies by the same group. This leads to some undefined issues in the study design.

The choice of two groups of patients (lean & obese) and the exclusion of overweight patients is indeed cited as a limitation on the discussion section; however it does require an adequate explanation in the “study design” section. Lines 92-101 describe a comparison between these two groups – if it is a previous one it should be in the introduction and shortened, if this is part of the present study – it should be incorporated into the “results” section, and be accompanied by the p-values and possibly a table (a revision of table 1 to show also subgroup specific data and p-values).
Several background explanations should be edited out of the methods study and incorporated either in introduction or in discussion, as appropriate. For example:
•	Lines 105-114 from “Previous research has shown…” to “such as the questionnaire used in the present study”.  Or at least until line 109.
•	Lines 97-99 – explanation of prior research should be in introduction unless a specific method cited in this article is utilized in current study. Lines 116-124 – a little too lengthy, should consider referring to appendix.

The comparison of PEI-UPS to total fat intake and total energy intake is not mentioned in the methods, although is discussed in results section and mentioned in the abstract under “Methods” (“The ability of these dietary indices to predict gestational weight gain was also compared with the predictive abilities of total energy intake and total fat intake”).

Specific comments:
•	Lines 84-87 – the authors do not address the difference in the 2 prenatal visits, and therefore the reader cannot assess the importance of the fact that on average there was no difference in gestational age. If, for example this is relevant for GWG assessment than some data about the average interval between visits could be more appropriate.
•	Lines 158-161 – exactly repeat lines 87-89 without adding information relevant to the statistical analysis of these outcome measures.
Validity of the findings: “Results” section -
Even though this is an analysis of pre-published data the results section should be wholesome and represent all information regarding results. Number of patients recruited, how many in each group (lean/obese) etc. prior to presenting table 1.
Specific comments –
•	All data should be presented with p-value in the text, even if p-value appears in table (example line 217-218, 220-221, 223)

“Discussion” section –
The comparison between HEI-2010 and PEI-UPP discussed in lines 275-284 is unclear and partially inconsistent with data presented in table 5. Lines 277-278 state that PEI-UPF (note spelling mistake since this line says UPP) is a better predictor of neonatal body fat percentage which is consistent with the table (although requires p-values in the text and referral to table).  However according to table 5 for skinfold thickness at the subscapularis both tests are significant (and HEI-2010 even with a lower p-value!), and for the thigh both are non-significant. Therefore when stated in live 278 that PEI-UPF is a better predictor in all these categories it is not clear on which statistical parameter the authors rely for this statement (they do not refer to any tale or p-value at this section). Additionally in line 281 the p value stated for association of HEI-2010 with body fat percentage is stated to be 0.334 whereas in table 5 it is 0.3 and the value of 0.334 cannot be found elsewhere in the data.
Line 303 – not only pregnant women may underreport food intake, it is a human tendency. The words “subjects” or “participants” is probably more appropriate.

“Conclusions” section –
The conclusion sections should briefly outline the main findings of the study without repeating general observations already presented in the discussion. Therefore should consider omitting lines 315-317 (from “excessive gestational weight gain”…”to “associated comorbidities”) and  lines 319-320 (from “thus, from a clinical standpoint…” to “that energy”).
Additional comments: This study is addressing important issues regarding maternal nutrition during pregnancy and its effect on maternal gain weight and neonatal obesity measures. This field is of growing interest in many countries.


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: RELATIONSHIPS BETWEEN CONSUMPTION OF ULTRA-PROCESSED FOODS, GESTATIONAL WEIGHT GAIN AND NEONATAL OUTCOMES IN A SAMPLE OF US PREGNANT WOMEN
Review round: 1
Reviewer: 2

Output:
Basic reporting: Manuscript : 18220v1
Title” Relationships between consumption of ultra-processed foods, gestational weight gain and neonatal outcomes in a sample of US pregnant women”
1. Title: It is clear.
2. Abstract :  Background, Methods, Results are Ok  .
 In "Discussion":
1) Spell out "PEI-UPF".
2) The first sentence   should be more specific.
3) Instead of 'several maternal outcomes", the authors should say "increase gestational weight gain" .
4) Instead of " several neonatal clinical outcomes", the authors should say" increase neonatal body fatness"
3. Introduction: It is clear and to the point.
4. Method : It is very well written and clear.
 5. Results and Discussion are very well written
6. Conclusions: It should shortened. I suggest to delete the two sentences on line 315 and 319 that start with “Excessive gestational weight….” and ends with “ food consumed.”.
7. References are pertinent and updated.
8. Tables and Appendix are OK.
Experimental design: "No comments"
Validity of the findings: The results are novel and important.
Additional comments: Important article that demonstrates that diet quality seems to be more important than the amount of food consumed in pregnancy.


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: RELATIONSHIPS BETWEEN CONSUMPTION OF ULTRA-PROCESSED FOODS, GESTATIONAL WEIGHT GAIN AND NEONATAL OUTCOMES IN A SAMPLE OF US PREGNANT WOMEN
Review round: 2
Reviewer: 1

Output:
Basic reporting: NA
Experimental design: NA
Validity of the findings: NA
Additional comments: The authors have revised the manuscript in accordance to our previous comments, and is now vastly improved.


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

Input:
Title: THE IMPACT OF CHOOSING WORDS CAREFULLY: AN ONLINE INVESTIGATION INTO IMAGING REPORTING STRATEGIES AND BEST PRACTICE CARE FOR LOW BACK PAIN
Review round: 1
Reviewer: 1

Output:
Basic reporting: This article is generally well written, appropriately referenced, conforms to PeerJ standards for structure, and has clear tables.

There are three areas where I believe the basic reporting could be improved:

1)	The way in which the intervention groups are described is frequently confusing, both within the abstract and the paper itself, for example “to compare the effect of receiving imaging results with best practice care (without imaging)”. I suggest rewording this with something along the lines of ‘to compare the effect of receiving imaging results with the effect of receiving best practice care that does not include imaging’. It may be helpful to provide a numbered list of the primary aims in the same way the secondary aims are presented.

2)	The last sentence of paragraph four in the introduction “Also of interest is evidence that providing patients with information about normal results - prior to their receipt of their own results - may optimise the reassuring potential of normal findings” is discordant with the previous paragraph that suggests imaging is not reassuring. I suggest rewriting the sentence.

3)	It would be useful to have exemplars of the pre-information, the normal scan report, the epidemiological information, and the enhanced report that were provided. These could be added to supplement 4 or 7.
Experimental design: I have two key queries in relation to study design that it may be helpful for the authors to address in the discussion:

1)	Why was a best practice care plus imaging group was not included?

Although I am not a proponent of scanning for reassurance, I could imagine that if I was I might also consider that I do this in addition to providing best practice care (excluding the explanation that scans are not helpful). This means that I could look at these results and see that best practice care was well received, but also that scores in the scan groups appeared to improve rather than deteriorate after receiving scan reports, so there is a possibility that receiving both of these interventions could be helpful. This dichotomy is carried over to the discussion where it is inferred that GPs choose between either scanning or providing explanation, rather than being able to provide both.

2)	Why was the TSK-11 was not completed at baseline?

With no baseline scores it cannot be assumed that the small differences between group found post-intervention are related to the intervention. It is also uncertain whether these between group differences are meaningful (given a four-point change in TSK-11 score is needed to identify an important decrease in fear of movement (Woby et al. 2005) ).

I have some additional queries and suggestions for the authors’ consideration.

3)	In terms of participants, were health professionals and other academics included in the authors’ networks and eligible to participate? This may have biased the results as these people may share similar views about imaging to the authors. The risks and benefits of using these networks could be discussed in the strengths and limitations section.

4)	Was there any assessment of the psychometric properties of the BRP (which I assume was developed for this study). These could strengthen interpretation based on changes in this measure.

5)	When and why was the Back Pain Attitudes Questionnaire completed and what were these data used for? These data are not currently presented.
Validity of the findings: The data generally appear to be robust, however, I am not qualified to comment on the statistical analysis.

1)	It would be useful to have mean change scores and 95% CIs presented for the ANCOVA analyses.

2) The sentence “This study provides evidence that simply offering best practice care is indeed effective management for recent-onset LBP” considerably overstates the results from this study as no one with recent onset LBP was included in the study and no clinical outcomes were measured.
Additional comments: Thank you for asking me to review this paper. It is an interesting study design and makes innovative use of technology to explore a hypothesis in a large sample of people. The paper is generally well written and related to current literature and thinking. Given the design, my impression is that the results can only be exploratory and the strength of these is overstated at times in the discussion.

Overall, I think that this paper makes a useful contribution to the knowledge base, and I am supportive of its publication, however, there are a number of places where I think it may be challenged and these may benefit from being addressed.


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

Input:
Title: THE IMPACT OF CHOOSING WORDS CAREFULLY: AN ONLINE INVESTIGATION INTO IMAGING REPORTING STRATEGIES AND BEST PRACTICE CARE FOR LOW BACK PAIN
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall the article demonstrated a clear, professional and unambiguous  English language.In order to improve the clarity I suggest that the author rewords line 5 to 8 in the background section to make the aim less ambiguous. The sentence line i282 is rather awkward and should be restructured,.
Appropriate literature reviews, references and context of this novel work in order to address gaps in the literature, Good links to the high prevalence of degenerative disease in asymptomatic individuals and potential for harmful misinterpretation of imaging. In order to provide more context on the role of imaging I would suggest referring to current guidelines for the use of imaging in LBP to identify cases where imaging is indicated and when it is not. Also add a line to clarify that most cases of LBP are self-limiting and subside within a particular timeframe and does noit require investigations..
Professional article structure, tables and raw data appears to be accurate and clear.
Relevant results were given to confirm the  hypothesis
Experimental design: This study is an original primary research within the scope of the journal.
Research aims and secondary aims were well defined, relevant & meaningful. It is stated how research fills an identified knowledge gap. You did not define the research question but identified the knowledge gap being investigated and the study contributes to filling that gap.
Appropriate and novel investigation performed to a high ethical standard. simulated patient, 3-armed, randomised online experiment.

However, how valid and reliable is his simulated patient approach  compared to real life patients this needs to be justified. Are there any reviews or studies looking at this? If so I would add to the methodology section. You mentioned that many adult volunteers suffered with LBP but did not indicate the severity or disability associated with this.. You could have included information on participant levels of anxiety or depression, work status and hobbies since these factors could have affected the results. Perhaps add more detail regarding the back pain questionairre and how that impacted upon the results.
Methods described with sufficient detail  to replicate the study.
Validity of the findings: Data is robust overall and clearly presented, a sample size calculation was performed the dtests utilised were statistically sound. The participants were randomised, and  blinded to the other interventions..

The  Primary outcome measure used was the BPS Line 149. Has the validity and reliability of this measure been established? If so it needs to be stated. What was the authors rationale  for combining the 3 numerical rating scores. This needs to be stated.
The data on which the conclusions are based are provided  and is statistically sound.. Appropriate discussions made  where rationale & benefit to the literature and patient management in primary care is clearly stated.

Conclusion are well stated, linked to original research aims & limited to the authors supporting results and the limitations of this study using simulated patients has been addressed.
Additional comments: This is an interesting and novel study with acknowledged limitations but has a sound conclusion and clear implications for primary care practice in the management of low back disorders.


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

Input:
Title: THE IMPACT OF CHOOSING WORDS CAREFULLY: AN ONLINE INVESTIGATION INTO IMAGING REPORTING STRATEGIES AND BEST PRACTICE CARE FOR LOW BACK PAIN
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The authors have appropriately addressed the comments and suggestions.


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

Input:
Title: THE TETRAPOD FAUNA OF THE UPPER PERMIAN NAOBAOGOU FORMATION OF CHINA: 1. SHIGUAIGNATHUS WANGI GEN. ET SP. NOV., THE FIRST AKIDNOGNATHID THEROCEPHALIAN FROM CHINA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript has been improved since last I reviewed it, and my comments are fewer, see below. I remain unconvinced that this is not just a Chinese specimen of Annatherapsidus, but at this point the authors and I will just have to agree to disagree on this point. In particular, though, I have doubts as to the presence of eight upper postcanines in this specimen. On the right maxilla there are only five alveoli, and that large of a discrepancy in tooth count between sides would be highly unusual in a therocephalian. It is difficult to see the alveoli in the figure provided, and it appears the alveoli in the left maxilla may not be fully prepared. A better figure of the specimen in palatal view would greatly improve this situation and make the identification as a new taxon much more convincing.

Line 12: “well know” should be “well-known”
Line 18: “akidnognathid” is misspelled
Line 19: “one species is known from Russia”—incorrect. There are two species of Annatherapsidus from Russia (A. petri and A. postum). (Furthermore, there are other Russian therocephalians that may be akidnognathids based on some phylogenetic analyses, e.g., Scylacosuchus.)
Line 30: “component” should be “components”
Line 35: “represented by a few species”—well, there are 55 named species of these therocephalians, none of which have been formally synonymized outside of an unpublished PhD thesis, so it is hard to say. I agree that once all the revisionary work is done there will be few left, however.
Line 68: As noted above, multiple species of Annatherapsidus from Russia are known. See Ivakhnenko (2011).
Line 87: “von Nopsca” should just be “Nopcsa” (note spelling)
Line 170: “is much robust” should be “is much more robust”
Lines 203–204: “Middle Permian” and “Late Permian” are no longer formal chronostratigraphic subdivisions, please use the informal “middle Permian” and “late Permian” instead.
Lines 209–211: Change this sentence to “Although middle and late Permian deposits in China have revealed a diverse, species-rich vertebrate fauna, therocephalian records have proven elusive.”
Line 264: Throughout this paragraph the family names Akidnognathidae and Perplexisauridae need to be capitalized. Also, why is it called Perplexisauridae when Figure 5 (and existing therocephalian literature) calls this clade Chthonosauridae?
Line 288: “akidnognathid” should be “akidnognathids”
Figure 1: It would be easier to interpret this figure if you note the type locality of Shiguaignathus by listing the genus next to the dot, like you do for Gansurhinus and Daqingshanodon.
Figure 5: “Euchambersia” and “Lycideopidae” are misspelled. Also, the genera “Ophidostoma” and “Microwhaitsia” are currently unpublished. Unless you are absolutely certain that these names will be published before the Shiguaignathus manuscript, please replace these names with the respective specimen numbers so as not to create nomina nuda.
Experimental design: See above.
Validity of the findings: See above.
Additional comments: No additional comments


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

Input:
Title: THE TETRAPOD FAUNA OF THE UPPER PERMIAN NAOBAOGOU FORMATION OF CHINA: 1. SHIGUAIGNATHUS WANGI GEN. ET SP. NOV., THE FIRST AKIDNOGNATHID THEROCEPHALIAN FROM CHINA
Review round: 1
Reviewer: 2

Output:
Basic reporting: Liu & Abdala present a well-preserved palate and snout of a putative new taxon of akidnognathid therocephalian. The overall presentation and illustrations are good, although they would benefit greatly from comparative photos of other akidnognathids and close-up illustrations of some of the purported anatomy, especially the dentition (or what little of the dentition is preserved).
Experimental design: The experimental design is good and follows standard geological, paleontological, and phylogenetic procedures.
Validity of the findings: The findings are important and convincing with regards to the presence of an akidnognathid therocephalian in this fauna. However, I have some questions about the generic diagnosis and justification of the new taxon (see detailed comments below).
Additional comments: I congratulate the authors on their discovery of a very nice centerpiece specimen for this study, and on the excellent presentation of their paper. Regarding my specific concerns, I want to make clear to the authors & editors that I have reviewed a previous version of this manuscript that was submitted to another journal. At the time, I did not feel that it merited publication in its current form because the major claim that the authors were erecting a new taxon was not justified by the available information in the fossil as illustrated. Since then, there's been some effort to address my concerns, although the authors continue to treat the specimen with a new genus name. I take issue with most of the characters in their diagnosis, but recognize that one or two subtle proportional traits could be useful in erecting a new taxon, and I am open-minded about these--namely the possibility of a high postcanine count and the obviously small size of the suborbital vacuity.

Taking on the the 'Diagnosis' point-by-point, the shape of the choana looks identical to the Russian Annatherapsidus and other early akidnognathids (it is not autapomorphic as their Diagnosis suggests), the extra palatal ridges are also present in Olivierosuchus and Promoschrhynchus (and perhaps others), and the postcanine tooth number appears at first consistent with the primitive number (6-7) based on the photographs, although they dashed-in extra putative alveoli in their drawing that suggest as many as eight postcanine positions--note that a previous version of the manuscript presented only 6 on one side and 7 on the other, which would be consistent with Akidnognathus. Given the ambiguity, I'd like to see this better illustrated with a close-up photo before I am convinced of this, but I suppose it's possible there may be up to eight.

The most convincing evidence of a new taxon is in the extremely small suborbital vacuities. I agree with the authors in that I have not seen vacuities this small in another akidnognathid specimen, so perhaps the authors are on to something here. Maybe the importance of this structure should be emphasized for now as evidence of a new taxon until more complete specimens are found in the future?

Overall, the new record adds important information about the biogeography and biochronology of Permian therocephalians, and I think it should be published in some form. I will make the recommendation to publish with minor revisions, pending that the authors can (1) add one or two useful comparative photos from the palates of other specimens, (2) better illustrate the dentition to support their claim about the high number of postcanines, which is not super convincing right now, and (3) revise the Diagnosis accordingly. There are also a number of minor spelling/grammar errors in the manuscript and figures (e.g., Lycideopidae is misspelled and placed at the wrong node in the cladogram) that the authors/editors will need to address at some point, as I am only commenting on the manuscript's scientific value at this point.

Thank you and good luck!

Adam Huttenlocker
University of Southern California


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: MASS MARKING OF JUVENILE SCHIZOTHORAX WANGCHIACHII (FANG) WITH ALIZARIN RED S AND EVALUATION OF STOCK ENHANCEMENT IN THE JINPING AREA OF THE YALONG RIVER
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper presents a detailed study on stock enhancement of S. wangchiachii and is written in a clear and concise manner. I would have liked to see a more precise definition of stock enhancement as well as a reference that shows such marking techniques are still clearly visible after several years in some species, e.g. in the otoliths of Acanthopagrus butcheri alizarin complexone was still visible after 15 years (Cottingham et al., 2015). I would also like to have more information on the species, such as maximum size and age and its importance as a targeted species.
The figures and tables are clear, however, I suggest smaller font on Table 2 would enable the table to be on one page instead of three. There are also some inconsistencies in spacing.
Experimental design: The experimental design was well thought out and executed and within the scope of the journal. The research question was well defined and fills an important knowledge gap. However, the description of the statistical analyses was not sufficient. This section needs to be expanded. Also, in the material and methods it needs to be reiterated that the means of the instantaneous growth and mass were calculated for different batches, otherwise it is not clear to the reader how statistical analyses can be undertaken.
Validity of the findings: The study demonstrates that restocking can be used as an effective measure to enhance the population of this species. The data was robust in that enough replicates were employed to undertake statistical comparisons.

It was concluded that this study offered a cost-efficient method for mass marking, but the costs are not discussed in the text.

Also, there is nothing in the introduction about total length, mass and condition factor and what these measurements represent, their meaning and why such measurements should differ between marked and unmarked fish.
Additional comments: I outline some general points below.
Use mm throughout instead of cm. No dash required between numbers and units.

Line 29. It is not clear what slightly increase means.
Line 43. otolith marking should be mentioned first as it is the most important in your paper. The same goes for fluorescent marking in line 46.
Line 137 Of the 600,000 marked fish, why were only 400,000 released.
Line 153/154 Consider rewording sentence.
Line 174 Three pairs, do you mean Sagitta, Asteriscus and Lapillus? If so, which ones did you mainly use.
Line 196/197 different font and double spacing
Line 229 The slight difference was statistically different, which one was less.
Line 234-242 What about condition factor between marked and unmarked fish.
Line 253 are the instantaneous rates unitless?
Line 323 What is the relevance of this?
Table 1 caption- treatments spelt wrong.
Figure 4 caption. Consider rewording


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: MASS MARKING OF JUVENILE SCHIZOTHORAX WANGCHIACHII (FANG) WITH ALIZARIN RED S AND EVALUATION OF STOCK ENHANCEMENT IN THE JINPING AREA OF THE YALONG RIVER
Review round: 1
Reviewer: 2

Output:
Basic reporting: This ms fulfills the criteria given.
General comments: An interesting and most clear paper on an important problem, i.e. how to evaluate the outcome of massive restocking activities using young/small fish individuals.
My main concern, besides some details below, is that the paper is unnecessary long and complex. The main reason is that so much statistics is presented not only in the tables, but also in the running text. Please consider to omit most of those details in the text, but comment on them using a reasonable amount of details and “digits”.
I am not that familiar with this journal and it rules, so the following are most as questions and suggestions;
•	As the same words and terms appear in both the title and as listed key-words, the key-words may be changed to increase the chance of being found in a search.
•	Seems the references seem to come in the wrong order when several are given within brackets in the running text, i.e. the come in alphabetic order and not in time order that is the most? common way in scientific papers.
Experimental design: Seems OK with me. In a way there are even two control groups, one is the unmarked fish stocked in the river and the other one are the groups held in ponds, where I assume life and growth is more "comfortable".
Validity of the findings: OK, but as statistics is not my expertise I cannot judge that part in any details, but looks convincing to me. Seems the results are so obvious.
Additional comments: See above (1. Basic reporting)


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: STEM-LOOP STRUCTURE PREFERENCE FOR SITE-SPECIFIC RNA EDITING BY APOBEC3A AND APOBEC3G
Review round: 1
Reviewer: 1

Output:
Basic reporting: In this manuscript, Sharma et al. have examined the role of stemloop structure and sequence in A3A/G activity. The work follows up on previously published findings by the group that A3A can edit RNA in monocytes and macrophages. In this manuscript, the impact of RNA shape and sequence is examined.
Experimental design: I found experimental design to be quite standard and sound.  A3A can be purified from eukaryotic or prokaryotic expression systems, and in the present work the authors have used a C-terminally His-tagged version purified form a bacterial expression system.  This protein is incubated with the RNA substrates, mutations are measured by sequencing.  Overall, the protocol follows established assays and data analysis was sufficiently detailed and rigorous.
Validity of the findings: The study identifies important structure and sequence aspects of the RNA substrates. The data is in line with the well-established sensitivity of all AID/APOBEC family member enzymes to ssDNA shapes and sequence motifs.  The functional data correlated nicely with predicted RNA secondary structures in a manner expected from the known biochemical properties of AID/APOBEC family member enzymes. I did not find grounds to doubt the validity of the presented findings.
Additional comments: In general, I found the manuscript was very well put together, clear and easy to follow. The conclusions are supported by the data and the work was rigorously carried out.  My suggestion to the authors are to include additional more comprehensive references:

-For instance, in regards to the role of A3s in viral restriction, there is an emerging body of evidence that A3s can also do the opposite, by helping retroviruses escape from drugs and adaptive immune recognition (suggested reference Monajemi et al. 2012, Retrovirology)

-In regards to the structure/function of A3 catalytic motifs as discussed in the introduction, there are some nice current structural studies focusing on the catalytic pockets of AID/APOBECs which can be referenced (e.g. King et al. 2017 Frontiers Imm, King et al. 2015 Structure, Shi et al. 2017 NSMB)

-The discussion will be improved if the authors also discuss their work in the context of previous works on the relative importance of secondary structure vs. primary sequence for determining AID/APOBECs. For instance, Larijani et al. 2007 MCB (amongst others) did similar work on AID and found that secondary structure (shape)  is a more important determinant of AID targeting to stemloops and bubbles, as compared to its trinucleotide WRC sequence specificity.


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: STEM-LOOP STRUCTURE PREFERENCE FOR SITE-SPECIFIC RNA EDITING BY APOBEC3A AND APOBEC3G
Review round: 1
Reviewer: 2

Output:
Basic reporting: Very minor comment on the references: it is a bit strange that introduction starts by citing reviews, which is perfectly fine considering the time passed from the initial characterisation of the APOBEC3s, yet only one review of the many labs involved in the initial characterisation (with a few still working on the APOBEC3 genes) is used.
Then the introduction moves to describe the APOBEC3 locus, going back to an original paper (Jarmuz 2002 - incidentally the organisation A3 locus described in that paper is different from the current understanding), but Jarmuz 2002  is not the proper reference for the Zn-coordinating residues in the deaminase domain (it should be Betts 1994).
Experimental design: no comments
Validity of the findings: The findings support the conclusions, pending the clarification of the problems highlighted below:
a) lack of negative controls
- With regards to the experiments with patients' MEPs, it would be useful to also have a sample in which APOBEC3A is silenced (the same authors have used siRNAs in the past). In Figure 1 there are background peaks in the chromatograms from Donor 2 and 3 HI that are the same height as the edited peak. It seems that even the edited peak could be considered background (which does not interfere with the conclusions)
- With regards to the in vitro experiments and the A3G ones, it would be necessary to use a catalytically inactive mutant of the enzyme to show the background levels of editing.
All this is necessary as it is not clear what is the dynamic range and the linearity of the editing assays.
b) It is not specified how many times the experiments were repeated, and there is no sign of error bars (or statistics) in any of the experiments.
c) in parts of Fig.1 the editing of the mutants is quantified through different methods (Sanger sequencing, AS-RT-qPCR). How do these assays compare with each other? Could it be better to keep the experiments separated?
Additional comments: The topic is fascinating and the findings have the potential to help us understand the dynamics of APOBEC-mediated RNA editing.
The striking observation that specificity and strength of RNA editing seems to be deriving from a segment of 10-16 nucleotides is somehow at odds with the specificity of editing previously described. How can such specificity be conferred by a few bases in the loop? What other elements are necessary for other the editing to be targeted to those transcripts?
Considering the data the Authors have accumulated in these years, it might be worth reanalysing the RNA-seq data and seek whether other transcribed sequences bearing identical stem-loop segments lack some other feature present in the edited transcripts.


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: STEM-LOOP STRUCTURE PREFERENCE FOR SITE-SPECIFIC RNA EDITING BY APOBEC3A AND APOBEC3G
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The rebuttal of the Authors answers most of my criticism. Yet I wonder why none of their argumentations end up in the manuscript. I would have thought some of those answers would provide context to the presented work and deserve a place in the study.

Specific comments:
- as I have already written, the background peaks in Donor 2 and 3 do not change the interpretation of the phenomenon, but they do cast doubts on the background levels of the assay and therefore on its dynamic range. In short, if you want to use a live cell assay to study biochemistry, you have to define the dynamic range of your assay, otherwise all your observations are just qualitative (which might be fine, but it should be noted). This is something the Authors should deal with.

- I apologize for missing the number of times the experiments were repeated (though it is not the usual notation) and the standard deviation. Would it be meaningful to add some statistics to describe the various efficiencies?

- Do the authors realize that maybe not every reviewer/reader is familiar with Supplementary Fig. 8 of Sharma 2015? It might be helpful a citation in the text to support the correlation between the two techniques. Moreover the slope in Suppl. Fig 8 is 0.7. Does this mean that the values were normalized between experiments in order to compare the two techniques? Would it be useful to label each substrate to highlight which experiments the data came from?

- Actually (aside from correcting the Betts reference), the references were just fine. It was just odd that the only original work cited at the beginning was the Jarmuz paper, whose importance with regards to the research presented is marginal if compared to other original research (e.g Sheehy 2002, Harris 2003, Mangeat 2003, etc.). It was odd, but a legitimate choice.
On the other hand, if Jarmuz is there because it is the first reference for A3A, then it would be fair to also cite the original Madsen 1999 [phorbolin] and Sheehy 2002 [identification of A3G] papers.


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: COMPARISON BETWEEN RADIAL ARTERY TONOMETRY PULSE ANALYZER AND PULSED-DOPPLER ECHOCARDIOGRAPHY DERIVED HEMODYNAMIC PARAMETERS IN CARDIAC SURGERY PATIENTS: A PILOT STUDY
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment.
Experimental design: no comment
Validity of the findings: In figure 4, besides Bland-Altman plots, linear regression plot with Pearson’s r2 coefficient should be shown to address the CO and SV measured by the two different methods.
Additional comments: This paper is well designed to address the priority of the  DMP-life vs. TTE and showed convincing data for the accuracy of DMP-life, which could be a proper candidate for the hemodynamic detector for the patients. I recommend the author add more statistical graphs like the linear regression plot with Pearson’s r2 coefficient in Fig.4.


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: COMPARISON BETWEEN RADIAL ARTERY TONOMETRY PULSE ANALYZER AND PULSED-DOPPLER ECHOCARDIOGRAPHY DERIVED HEMODYNAMIC PARAMETERS IN CARDIAC SURGERY PATIENTS: A PILOT STUDY
Review round: 1
Reviewer: 2

Output:
Basic reporting: Minor comment:
In the exclusion criteria, please confirm the information of LVEF: 40% or 45%?
Experimental design: No comment.
Validity of the findings: The authors of current study well described their work and got the conclusion.
Additional comments: As an alternative choice of pulmonary artery catheter or transthoracic / transesophageal echocardiography measurement, non-invasive radial artery tonometry test has been introduced and functionally well described to measure the aortic pressure, artery stiffness or heart function during the past 20 years. However, less than 20% (107/572) total operated patients could use this method shows that it still need to be well evaluated before widely usage.


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: COMPARISON BETWEEN RADIAL ARTERY TONOMETRY PULSE ANALYZER AND PULSED-DOPPLER ECHOCARDIOGRAPHY DERIVED HEMODYNAMIC PARAMETERS IN CARDIAC SURGERY PATIENTS: A PILOT STUDY
Review round: 1
Reviewer: 3

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: In this manuscript, Zayat et.al first time compared the DMP-life tonometry device measured SV and CO with TTE in preoperative cardiothoracic surgery patients. Their data indicate reasonable accuracy and precision between two technologies. Manuscript is well written and experiments are straightforwardly designed, but the conclusion needs more data to support. Following is my concerns:

1.	Authors only used the Bland-Altman analysis to compare the differences between TTE and DMP-life measurement (both SV and CO). Linear regression analysis to illustrate the correlation efficiency can be considered to compare these two methods.
2.	In the discussion section, authors discussed the advantages and disadvantages of TTE and DMP-life. But to better explain the feasibility of DMP-life, authors can compare their data to other reported SV/CO monitoring methods. For example, Castro et al (Castro V De, Lhotel L, Mabrouk N, Perel A, Coriat P. Comparison of stroke volume (SV) and stroke volume respiratory variation (SVV) measured by the axillary artery pulse-contour method and by aortic Doppler echocardiography in patients undergoing aortic surgery. 2006;97: 605–610.) compared SVs measured by the axillary calibrated artery pulse-contour method with TTE, and their percentage error of both minimum and maximum SV was 26%.
3.	According to a lot literature, many SV/CO monitoring devices have not yet replaced PACs due to poor trending ability. Authors better to have serial measurements at different hemodynamic states (instead of single measurement) to assess trending ability, and analyze ΔSV values using four-quadrant plot or a polar plot analysis.


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: COMPARISON BETWEEN RADIAL ARTERY TONOMETRY PULSE ANALYZER AND PULSED-DOPPLER ECHOCARDIOGRAPHY DERIVED HEMODYNAMIC PARAMETERS IN CARDIAC SURGERY PATIENTS: A PILOT STUDY
Review round: 1
Reviewer: 4

Output:
Basic reporting: The aim of this study is clear that the authors tried to use the non-invasive BPPA to replace PWD method in clinics especially in cardiac surgery patients.
Experimental design: There were some data showed the mean CO and SV were comparable between BPPA and TTE in coronary artery bypass surgery patients. However, there are no data to show the sensitivity and accurate/reliable dynamic range of BPPA.
Validity of the findings: The concept and data in the manuscript are original and useful for clinics. It is much easier to get cardiac and hemodynamic information using this non-invasive way than conventional TTE. Thus, patients will benifit much if this method will be widely used in hospitals.
Additional comments: The authors tried to compare the accuracy and reliability of BPPA used in cardiac surgery patients. Over all, this manuscript is well organized and the data are clearly presented. However, there are some places need to be improved:

1) Figure 1 can be removed from the manuscript. Although it shows some standards that exlude the patients from BPPA test, it does not have any information about the 107 patients enrolled in the test, which should be the key information other than the excluded ones.

2) Figure 2 shows the principle of DMP-life system, however, there were not any explanations in the text. Can the authors add some information to explain the key principle of this system and how it is used in patients.

3) Figure 3 shows the results were got at different applied pressure for each tested patients. What do red rectangles and arrow mean in the figure? The shape are different at different pressure for different persons, so is the shape related to the severity of the heart disease?

5)  In Figure 4, the description of the figure legend and the titles in the figure are not consistent. Please check and make the figure in the right order and label.

5)  The authors only tested the applicability of DMP-life system in patients with cardiac diseases. Why did not you test it on normal people? so that then we can better know how reliable/accurat it is for this system. I encourage the authors add these data in to make the conclusion more solid.

6) Check the writing and format, and keep them consistent. For example, line 39 and line 193 "5.2±0.85" could be "5.2 ± 0.85".


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: COMPARISON BETWEEN RADIAL ARTERY TONOMETRY PULSE ANALYZER AND PULSED-DOPPLER ECHOCARDIOGRAPHY DERIVED HEMODYNAMIC PARAMETERS IN CARDIAC SURGERY PATIENTS: A PILOT STUDY
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: The article is ready for publish.


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: COMPARISON BETWEEN RADIAL ARTERY TONOMETRY PULSE ANALYZER AND PULSED-DOPPLER ECHOCARDIOGRAPHY DERIVED HEMODYNAMIC PARAMETERS IN CARDIAC SURGERY PATIENTS: A PILOT STUDY
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: The authors of current study well described their work and got the conclusion.


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: COMPARISON BETWEEN RADIAL ARTERY TONOMETRY PULSE ANALYZER AND PULSED-DOPPLER ECHOCARDIOGRAPHY DERIVED HEMODYNAMIC PARAMETERS IN CARDIAC SURGERY PATIENTS: A PILOT STUDY
Review round: 2
Reviewer: 3

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Thanks for the authors performed the pearson correlation efficiency analysis. But the correlation of CO measurements between DMP-life and TTE (r = 0.501) is not a good correlation, which means the CO measurement might be not accurate as TTE. Moreover, authors claimed that this study is to ensure the accuracy of DMP-life device without reproducibility analysis. Then it is very important for authors to include direct comparisons between DMP-life and standard PAC measurement (and can also compared with TTE), especially at this case, the CO measurements didn’t have a significant positive correlation.


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: COMPARISON BETWEEN RADIAL ARTERY TONOMETRY PULSE ANALYZER AND PULSED-DOPPLER ECHOCARDIOGRAPHY DERIVED HEMODYNAMIC PARAMETERS IN CARDIAC SURGERY PATIENTS: A PILOT STUDY
Review round: 2
Reviewer: 4

Output:
Basic reporting: The revised manuscript is well improved. The methods, results and discussion are more clearer.
Experimental design: n/a
Validity of the findings: n/a
Additional comments: The authors addressed my concerns and the manuscript was well improved.


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

Input:
Title: GENOME-WIDE IDENTIFICATION OF ABA RECEPTOR PYL FAMILY AND EXPRESSION ANALYSIS OF PYLS IN RESPONSE TO ABA AND OSMOTIC STRESS IN GOSSYPIUM
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: The manuscript submit by Zhang et al. regarding genome wide identification of ABA receptor protein family PYLs in four different species of cotton is an extensive report. Though the PYL family members are reported from many other plants, but the current report is the first from Gossypium spp. In spite of no novelty in the entire research the information generated will be of interest for researchers working with Gossypium spp. Apart from identifying the entire family members from  progenitor G. arboretum, G. raimondii they also identified them in the tetraploid G. hirsutum and G. barbadense species. The authors also performed the chromosomal location of each gene, synteny among all four species and phylogeny with PYLs of other known plants. The members of G. hirsutum was further investigated for its tissue specific expression, regulation under ABA treatment and osmotic stress. They also analysed GhPYLs interaction with two members PP2C proteins, GhABI1A and GsABI1D known to be involved in ABA signalling. Even though, the later part of the work is fragmented and ends abruptly, the information in the manuscript is interesting.
I have following minor concerns for the submitted work:
The nomenclature of the Gossypium PYLs are solely based on that of Arabidopsis PYLs. It seems this nomenclature (giving a specific number at the end) does not hold true when PYLs of rice is also considered. Can author take this opportunity to propose a uniform nomenclature of PYLs across different plant species.
Tissue specific expression of GhPYLs are compared with the expression of PYLs in root (Fig. 6). As such the modulation of these genes could not be assessed in root. It will be better if an house keeping gene is taken as internal control.
The Y2H analysis result may also be presented in tabular form, that will be easy to see in one glance which PYLs are interacting with the two selected proteins.


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

Input:
Title: GENOME-WIDE IDENTIFICATION OF ABA RECEPTOR PYL FAMILY AND EXPRESSION ANALYSIS OF PYLS IN RESPONSE TO ABA AND OSMOTIC STRESS IN GOSSYPIUM
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors have identified the PYL genes in Gossypium species. They have identified 21 genes in G.arboreum, 20 in G.raimondii, 40 in G.hirsutum and 39 in G barbadense. They have done thorough bioinformatics analysis of these genes, and have identified conserved secondary structure that are essential for the function for ABA receptors in arab.
They have analysed the G.hirsutum genes for the relative gene expression in osmotic stress and in response to ABA. Using two hybrid system they have also shown the interaction of GhPYLs and GhABI1A and GhABI1D.
Experimental design: The material and methods are clearly written.
Validity of the findings: The authors have done several experiments to validate the claims made in the manuscript. The relative gene expression shows the role of PYL in ABA response and osmotic stress. Similarly the yeast two hybrid analysis shows the interaction of PYL with Gh ABi1A and Gh ABI1D.
Additional comments: There was one paper by Chen et al published in PPB on the Overexpression of cotton PYL genes in Arabidopsis enhances the transgenic plant tolerance to drought stress. The authors have not mentioned this in their manuscript and since this paper is on PYL in G. hirsutum, the authors need to revise the manuscript accordingly.


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

Input:
Title: GENOME-WIDE IDENTIFICATION OF ABA RECEPTOR PYL FAMILY AND EXPRESSION ANALYSIS OF PYLS IN RESPONSE TO ABA AND OSMOTIC STRESS IN GOSSYPIUM
Review round: 1
Reviewer: 3

Output:
Basic reporting: No comment
Experimental design: Details were missed in some experiments. For example:

Line 148：Which parts of the plants were sprayed with ABA? How to treat with 10% PEG6000?
The paragraph of Line 144: You have both treated plants (after Line 145 which is clear to readers) and untreated plants (before line 145). Please make it clearer that the plants were not treated. The roots of the treated plants were sampled and frozen. How were the samples of the untreated plants treated after sampled?
Line 150: How many grams of the samples were used for RNA extraction? How were the samples homogenized before the extraction?
Line 151 and line 152: The reaction conditions of cDNA synthesis of RT-PCR? Please rewrite this part.
Line 155: “Experiments were repeated at least three biological replicates.” Do you mean the experiments were repeated at least three times? How many replicates did you have each time?
Line 154 primer: please provide primer sequences in Materials and Methods or in the supplementary
Validity of the findings: No comment
Additional comments: Generally, the manuscript is written in professional English with minor errors. The study is novel and meaningful. The introduction has sufficient background information.The hypotheses and experiment design are appropriate. But, details were missed in some experiments. The result section including figures and tables are generally OK. But, 1) the explanation of some results are not clear or sufficient; 2) the figure may not be a very good format to present the results shown in Figure 6, 7, and 8. The discussion is OK.
Please read the detailed comments and suggestions in the annotated PDF 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: GENETIC DIFFERENTIATION AND PHYLOGEOGRAPHY OF MEDITERRANEAN-NORTH EASTERN ATLANTIC BLUE SHARK (PRIONACE GLAUCA, L. 1758) USING MITOCHONDRIAL DNA: PANMIXIA OR COMPLEX STOCK STRUCTURE?
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No Comment
Validity of the findings: No comment
Additional comments: The authors use mtDNA sequencing to examine population structure between Mediterranean and Northeast Atlantic blue shark populations. The paper is interesting and will make a nice contribution to the literature. I have made comments and suggestions below.

General comments

Given the proximity of the populations, I was surprised the authors found genetic differentiation in their dataset. This is a very interesting result.

In some areas, the authors are a bit too verbose (examples: last sentence of Abstract; lines 76-80; lines 215-219; lines 237-242; lines 254-258; lines 316-330)

I commend the authors for the interactive map of their sampling—this is very cool!

Why were the sequences not combined to a concatenated sequence and the same set of analyses run? Also, why the discrepancy between sample sizes for the two genes?

Specific comments:

Abstract:

I suggest changing “failed in finding evidences of constant migrations” to “failed to find evidence of migration”

I suggest changing “The network results revealed apparently no genetic structure through the Mediterranean-Atlantic seaway, quite the opposite, the Phist AMOVA and pairwise Phist analysis found a significant genetic structure among four geographical groups” to “Although no obvious genetic structure was apparent from the haplotype network, Phist analyses indicated significant genetic structure among four geographical groups.”

Line 3: make “shark” plural and change “spreads” to “is found”
Lines 17-18: change to “on the western side” and “on the eastern side” (change “in” to “on” in each case).
Line 19: delete “and”
Line 55: delete period after Mediterranean
Lines 65-66: authors cite a study stating that almost all BS caught in the Mediterranean were immature, yet in their dataset (Table S1), this is not the case. The authors do not speculate as to why this is. It would be interesting to touch on this in the Discussion if the authors have any insight.
Lines 74-75: In the abstract, the authors state 8 populations—please clarify.
Line 80: change “Expected” to “These”
Lines 116-119: Normally, final concentrations are reported (this is a minor point).
Line 154: change “females outnumbered significantly males” to “females significantly outnumbered males”
Line 178: Which second one? It looks like only the haplotype with 61 individuals is shared by all populations except NNEATL (which is mentioned in lines 176-178).
Lines 231-236: which markers were used in these other studies and how do they relate to data here?
Lines 242-245: Do you mean female philopatry when you say “reproductive movements?” The mtDNA structure found could very well indicate this, although it would help to have corresponding nuclear data to verify. Also, the authors don’t really stress whether or not these sampling locales were nurseries (although they do mention in passing)—I would suggest explicitly stating which sites are known (or suspected) nursery sites—the authors do this for the Mediterranean but not the Atlantic sites. Also, I would suggest analyzing sites without adults—if female philopatry could explain these results, I would expect an even stronger signal when solely analyzing juveniles/immatures from each site.
Lines 258-260: This isn’t necessarily true—they can be panmictic (with males mating across populations) with female philopatry. Based on other studies, I’d be surprised if nuclear data exhibited structure. Following, (lines 266-268)—nuclear data may not necessarily exhibit structure.
Lines 269-283: This paragraph seems out of place. Most of it belongs in the INTRO.
Lines 316-330: Also seems a bit out of place, with a lot of this belonging in the INTRO. Ending with a comment on the fin trade doesn’t fit with this study. Instead, I would suggest stating the novelty of the Mediterranean population based on your results and how specific conservation measures should be implemented for the population (for example, leaving lines 321-325).

Fig 1: This is minor, but I suggest changing “sampling design” to “sampling sites” as some of these sites weren’t designed but were instead from commercial fisheries.
Fig 1: In both the figure (either on the figure itself or in the legend) and also in the text, please include sample sizes of the four regions.
Fig 2: I understand why the authors have multiple colors within certain haplotypes (for example, three green in haplotype 42), but without knowing the sample locales, these are meaningless. Since the authors break this down in the supplemental figure, I would suggest combining the colors for this figure.


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: GENETIC DIFFERENTIATION AND PHYLOGEOGRAPHY OF MEDITERRANEAN-NORTH EASTERN ATLANTIC BLUE SHARK (PRIONACE GLAUCA, L. 1758) USING MITOCHONDRIAL DNA: PANMIXIA OR COMPLEX STOCK STRUCTURE?
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper is nicely presented, has an adequate number of references and has a sufficient number of tables and figures. I have added minor suggestions for the authors.

Background
“but genetic structure has not been confirmed even at interoceanic distances.” Remove the word “even”. There are plenty of recent papers on BS describing genetic structure on an intraoceanic level.
Results
Remove “apparently” and replace “quite the opposite” with whereas.

Introduction
Line 3: Please use a reference for the previous statement.
Line 40: The authors use the term mating clubs. It might be better to include them into quotation marks.
Line 55: remove the first “.”
Line 71: Add a space before “On the other hand”

Material and Methods
Lines 87-90: Please add the number of individuals per sampling area in case readers will not have to check supplementary material.
Lines 110-111: Why did the authors required to design new primers for the species, since they could follow previous attempts? See Verissimo et al., 2017 for CR primers. Can they justify their decision?
Line 120: replace “annealing at 60ᵒC for 30s” with “annealing at 60ᵒC for 30 s”.
Line 139: Describe the four groupings for the AMOVA analysis.

Results
Line 179: What does the N≥10 mean? Number of individuals? Number of haplotypes? Please clarify.

Discussion and Conclusion
Line 244: Replace “Φsts” with “Φst values”.

Lines 252-253: I am wondering about the role of the Adriatic as a nursery for BS. The authors claim to confirm Megalofonou et al., 2009 suggestions about the matter. I also assume that the authors have probably used samples provided from the same dataset used in that manuscript. Considering the lack of information on sampling dates (I do not remember seeing a table with the actual dates that the samples were caught), have the authors compared the sizes or sex ratios based on time of capture? Do they have other individuals caught in the same period for direct comparison and subsequently prove their argument?

Figures and Tables
Figure 2: What is the point of the additional small figure displaying the size+number of individuals per haplotype, when you have the number of individual in each haplotype? Please remove it, as it does not add anything to the Figure.
Figure 3: You need to add the details for the sampling locations. NNEATL: North North-eastern Atlantic; SNEATL: South North-eastern Atlantic; WMED: Western Mediterranean; EMED: Eastern Mediterranean.
Experimental design: The importance of the sampling area is highlighted throughout the manuscript. The Mediterranean is a very important mating and nursery ground for chondricthyans. The methods are sufficiently described.

However, I was wondering about the sampling dates. Sampling took place from 2003 to 2016. Have the authors checked for temporal differences?
Validity of the findings: Despite the complexity of the results, the authors do a very good job describing and justifying their results. Their findings are robust. and statistically sound. There are a couple of things that need to be clarified.

There is a lack of discussion regarding the sex ratio differences found between the two seas despite the results they reported in Lines 154-164. Do the authors have any suggestions? Moreover, can you justify the differences in male/female sex ration found in the Mediterranean between your results and the ones reported by Megalofonou et al., 2009?

Lines 254-268: You are trying to justify the complexity in structure between the Mediterranean and adjacent North-eastern Atlantic BS. You are doing an excellent job by justifying your data with the results from tagging data (previous studies). Considering the lack of nuclear data, I believe that you can also use studies with similar distribution might partially help you justify this weak structure between the Med and the Atlantic. There are at least three papers (2 on Scyliorhinus canicula and one on Etmopterus spinax) that might be able to help the authors add to their discussion, particularly in the absence of nuclear data.
Additional comments: This is a nice study with sufficient mtDNA data that is well analyzed and well presented. The figures are clear. I feel that the study will be of broad interest to readers of the journal because of the interesting region being sampled. Our understanding of elasmobranch genetic structure is greatly improved by studies such as this. This is especially true in light of recent papers that have presented genetic structure in the Mediterranean.

I think there is the basis for a nice publication on the population structure of Prionace glauca, and I believe that the manuscript could be improved as few things are not presented adequately.


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: GENETIC DIFFERENTIATION AND PHYLOGEOGRAPHY OF MEDITERRANEAN-NORTH EASTERN ATLANTIC BLUE SHARK (PRIONACE GLAUCA, L. 1758) USING MITOCHONDRIAL DNA: PANMIXIA OR COMPLEX STOCK STRUCTURE?
Review round: 2
Reviewer: 1

Output:
Basic reporting: The paper is nicely presented and questions/concerns raised by both reviewers have been dealt with by the authors.
Experimental design: The importance of the sampling area is highlighted throughout the manuscript. The methods are sufficiently described.  I would like to thank the authors for the extra analyses they performed and replying to all questions raised.
Validity of the findings: My concerns from my previous review have been addressed.
Additional comments: This paper is a nice contribution to the literature, particularly for Mediterranean species.


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: ECOMORPHOLOGICAL INFERENCES IN EARLY VERTEBRATES: RECONSTRUCTING DUNKLEOSTEUS TERRELLI (ARTHRODIRA, PLACODERMI) CAUDAL FIN FROM PALAEOECOLOGICAL DATA
Review round: 1
Reviewer: 1

Output:
Basic reporting: refer to general comments for the author
Experimental design: no comment
Validity of the findings: refer to general comments
Additional comments: I recommend publication with minor revisions as listed below.

I am not familiar with the software programs used so I will not comment on their efficacy. I will list below comments and errors by their line number.

Ln 45	hypocercal instead of hipo-

Ln 49	founded instead of funded

Ln 72	pteraspidomorphs instead of pteraspidomorfs

Ln 103		Add Carr (2010) to the references about Dunkleosteus  inhabiting the seas of Euramerica.

Ln 110		Add Carr (2010) to the references, since it directly address the pattern of disarticulation in Dunkleosteus.

Ln 112		In line 333 you refer to Coccosteus as a “close related placoderm.” In this line you refer to Coccosteus as a ”smaller basal arthrodire.” Neither case is accurate. Coccosteus is a member of the coccosteomorph arthrodires while Dunkleosteus is a member of the pachyosteomorph arthrodires. These two groups are sister groups, thus neither is more basal to the other. Terminology more appropriate might be what you used to describe sharks as “non-closely related” since the two arthrodires are from distinct orders.

Ln 124		In this line you refer to type 1 and type 2 and direct the reader to Fig. 1A where you show the 8 landmarks. Is Fig. 1A the type 1 and Fig. 1B the type 2? You may want to note then that type 2 has two additional landmarks as noted in Fig. 1B. You could add this within the parentheses. Also, in the figure caption you should identify which figure represents type 1 and type 2 so that the text and caption parallel each other.

Ln 142		Add “v.1.4.1” to the software (tpsRegr v.1.4.1) to be consistent with your references to other software packages (e.g., tpsDig1 software v.1.4).

Ln 149		Elsewhere in the text you only refer to TBL, not BL (e.g., in line 188 and Supplemental Data S2).

Ln 153-154	The plate names will not be familiar to non-placoderm workers so it would help if you labeled those plates on your Fig. 1C.  As in Carr & Jackson, 2010: fig. 5-7, you can add SO, PN, and R to your Fig. 1C. For the site of the quadratomandibular articulation you can place an asterisk on the PSO plate. Be sure to define your abbreviations in the figure caption.

Ln 158		Since you use the abbreviation “JM” later (e.g., line 183) you should introduce it in this line, e.g., “five infergnathal metric variables (JM1-5).”

Ln 164-164	This sentence contains a double negative (No, with neither, nor).  Either use “no, either , or” or possibly “Significant phylogenetic signals have been detected neither…nor….”

Ln 165		Add a comma after sharks (“sharks, respectively).

Ln 166-167	Drop the article “the” before the percentages, i.e., “PC1 explains 41.7% of the total variance whereas PC2 explains 32.7%.”

Ln 193		In this line you refer to  “deep peduncles” while in line 341 you call it a “narrow peduncle.” Deep (to me) implies a wide peduncle so change line 193 to match line 341. Also in this line change hipocercal to hypocercal.

Ln 202		In the references, you list this as Thomson & Simanek, 1977.

Ln 212		Thunniform instead of tuniform (the same change elsewhere).

Ln 217		lobe instead of love

Ln 237		Change phrasing: I suggest “our work has allowed the establishment of a comparative framework”

Ln 246		bouyancy instead of bouayancy

Ln 258		Change phrasing:  “As in sharks”

Ln 307		founded instead of funded

Ln 280		thunniforn instead of tuniform

Ln 286		mechanisms instead of mechanism

Ln 294		Is your reference to the entire book by Boucot or more specifically to Williams, 1990, Feeding behavior in Cleveland Shale fishes, p. 273-287. In Boucot, Evolutionary Paleobiology of Behavior and Coevolution. I think the specific reference would aid the reader in finding the reference.

Ln 307		founded instead of funded

Ln 325		Spell out the first use of the genus name in C. carcharias.

Ln 333		refer to line 112 comment. Does membership in a separate but sister order make it “close related”?

Ln 341		refer to line 193 comment

Ln 343		Instead of “involves” would “implies” be more appropriate?

Ln 358		Usually references to a figure in another document use a lower case “f” while references to figures in the manuscript use an upper case “F”. What are the instructions to authors guidelines for PeerJ?

Ln 369-370	In line 513 you refer to Paul, Chase & Hodges, 1989 as Paul & Chase and note that it is in book edited by Hodges. Which is correct?

Ln 374		Use either “This kind of approach can be” or “These kinds of approaches can be”

Ln 384		Phrasing: “how” versus “what”?

Ln 384-388	This is a fragmented sentence. Can you break it up into two or more sentences? It is hard to follow as it is now.

I checked that all the references are listed in the text and visa versa.

Figure 1	As noted above, it would help the non-placoderm reader to add plate abbreviations for the SO, PN, and R as well as a possible asterisk for the site of the jaw articulation on the PSO (refer to Carr & Jackson, 2010:fig. 5-7). Again, my question of adding type 1 and 2 in the figure caption to match their mention in the text.

Tables 1&2	(JM1-5) instead of simply (JM)


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: ECOMORPHOLOGICAL INFERENCES IN EARLY VERTEBRATES: RECONSTRUCTING DUNKLEOSTEUS TERRELLI (ARTHRODIRA, PLACODERMI) CAUDAL FIN FROM PALAEOECOLOGICAL DATA
Review round: 1
Reviewer: 2

Output:
Basic reporting: In the interest of open and honest dialogue in science I do not wish to remain anonymous, and encourage the authors to contact me if they have any queries. Regards and best, Tom Fletcher, University of Leicester

•	Clear, unambiguous, professional English language used throughout.
Suggested improvements:

L28 - “However, body design of fishes is determined in a large extent …” should be “determined to a large extent”.
L29 - “… being possible to clearly recognize different morphological traits that have evolved several times in non-closely related groups with similar lifestyles” I would suggest should be “making it possible to recognise”. I feel clearly recognising is too general in that instance, as it is only very extreme adaptations that are obviously for a specific purpose.

L45 - “fin span or the hipocercal” should be hypocercal

L46 - “The application of this ecomorphological approach to the concrete case of Dunkleosteus terrelli has led to a new reconstruction of this emblematic placoderm.” It is unclear what you mean here, what is a concrete case?
L49 - “in contrast to classical reconstructions funded on the phylogenetic proximity with much smaller placoderms known from complete specimens” Funded is an inappropriate word here. I would suggest “… reconstructions based on the…”

L52 - “which entails that the caudal fins of placoderms could have displayed a greater range of morphological variability than thought up to date”. I would suggest “which suggests a greater morphological variability in placoderm caudal fins than previously thought.”
L55 – “The Fossil Record…” should not be capitalised, suggest “The fossil record…”
L55 – “…glimpse into the extinct creatures” is unclear, suggest “glimpse in to the lives of extinct creatures”.
L70 – Sentence a little long “However, large dermal plates are typically restricted to the cephalo-thoracic region in early vertebrate groups (e.g., placoderms and most agnathan ostracoderms including pteraspidomorphs, galeaspids, osteostracans and pituriaspids) and scales, that normally cover whole body surface, easily disarticulate being found as isolated elements in the vast majority of cases (Janvier, 1996).” I’d suggest “However, large dermal plates are typically restricted to the cephalo-thoracic region in early vertebrate groups (e.g., placoderms and most agnathan ostracoderms), and in the vast majority of cases scales disarticulate to isolated elements during preservation (Janvier, 1996).”
L76 – Some repetition here, and a little unclear suggest deleting “ leading in conjunction to a very vague 79 idea of the general body shape and size of a big number of early vertebrate representatives, 80 especially in regard to their post-thoracic region.” Instead explain briefly (7-8 words) that endochondral bone has a greater preservation potential (with reference).
L85 – ‘Fabricational’ is not an appropriate word here, do you mean ‘developmental’? Nevertheless  I would suggest “including not only the phylogenetic legacy of the species but also environmental and functional aspects (Seilacher, 1991).” I would use ‘species’ instead of ‘group’ here, since you are arguing (and I agree) that every species is uniquely shaped by the factors you list.
L86 – I suggest “… aquatic vertebrates is determined to a large extent by their swimming mode”
L88 – Suggest “… the functional constraints of different types of locomotion are so strong that…”
L93 – Suggest “…between the mode of life and body pattern in living aquatic vertebrates, we propose that the identification of ecomorphological relationships…”.
L96 – This is a very long sentence. Suggest “With this aim, we have assessed the relationship between the locomotory patterns and the morphological variability of the caudal region in extant sharks by means of geometric morphometrics and allometric regression analysis. We present a comparative framework for predicting some anatomical aspects in extinct species from palaeoecological data, and vice versa”
L103 – ‘Paradigmatic’ is not an appropriate word here. Suggest “Dunkleosteus terrelli is an exceptionally large and iconic carnivorous placoderm that inhabited the seas of Euramerica during the Late Devonian (Carr & Jackson, 2010).”
L106 – I suggest “Given its large size* and fearsome appearance, D. terrelli has been a focus of interest for the general public for decades.“. *I would also include a length in metres here, with reference.
L108 – Suggest “However, despite popular interest in the species D. terrelli is only known from disarticulated plates of the head shield, and a few articulated remains of incomplete pectoral fins (Carr, Lelièvre & Jackson, 2010).”
L111 – Suggest “ … remain unknown, and to date reconstructions of D. terrelli have relied on the morphology of smaller basal …”
L113 – I think the paragraph starting “As a consequence …” repeats the previous paragraph and I’d delete it
L128 – Suggest “This procedure allows the removal of variations in….”
L131 – Suggest “The degree of homplasy was checked by plotting … “
L163 – Should be “… of a Pinocchio effect …t”
L164 – Double negative, suggest “… detected either for the … “
L166 – Should be “…PC1 explains 41.7% of the total variance whereas PC2 explains 32.7%.”
L168 – Should be “… caudal fins of sharks …”
L184 – Should be “ … both variables shows a good fit to a linear model…”
L208 – This whole sentence is unclear and I think repeats what follows. If you want to keep this I’d suggest “The shark body patterns proposed by Thomson & Simanek (1997) are recognizable after our morphometric analysis. Separate groups, as extremes of a morphological continuum, are probably due to different locomotary styles (Fig. 2B).”
L214 – Should be “… adapted to strong continuous swimmimg… “
L217 – Should be “well-developed ventral lobe and wide …”
L224 – Suggest “There is evidence that increased size results in lower muscle contraction frequency (Altringham & Johnston, 1990; Altringham & Young, 1991), which results in lower tail beat frequency (Wardle, 1975). Consequently, a loss in swimming speed and hydrodynamic lift is compensated for with proportionally wider caudal fin spans (Motani, 2002; Lingham-Soliar, 2005).”
L233 – Suggest “where hydrodynamic lift is not as important, with decreased need to control …”
L237 – Confusing sentence, suggest “Our work is the first to establish a comparative framework with geometric morphometrics of body-caudal fin propulsion on which to base ecomorphological inferences of extinct early vertebrates.”
L240 – Suggest “… approach is applicable for …”
L245 – Suggest “… placoderms and ‘acanthodians’)…”
L247 – Should be “… that contribute to buoyancy … ”
L253 – Suggest “ … remains of large pelagic arthrodires… “
L254 – Suggest “… make it difficult to base…”
L258 – Unclear, I suggest “As in modern sharks, arthrodire…”
L260 – Suggest “ … as the main propulsor organ, are also be subject to strong selection pressures driven by ecology, locomotion and body size”
L266 – ‘In this sense’ is not the best way to phrase this, and th term cruising describes the contuous swimming. Suggest “Recently, Carr (2010) has provided strong statistical evidence for active pelagic cruising in this species, based on taphonomical and sedimentological data.”
L270 – Autocorrect has resulted in typos here “… Basin (EEUU) and the Tafilalt Basin (Morocco), suggesting a…”
L276 – Suggest “… modes could also be present …”
L287 – Suggest “… armoured animals, for example arthropods… “
L293 – Suggest “ … thus constituting direct evidence of the …”
L307 – Misuse of the word funded again, suggest “…placoderms have been based on the proportions of …”
L314 – To clarify I suggest “ …, including C. cuspidatus itself (Miles & …”
L318 – Typo, should be “ variables in placoderms (see Carr….”
L323 – I would try and reduce the length of this sentence.
L343 – This sentence is unclear, what outlines? I think this needs to be more specific.
L346 – This sentence does not provide additional information and repeats previous points. I would suggest deleting it. I am also unclear as to what is being suggested in the line 348 sentence starting “In this sense…”. Again not a common phrase in scientific writing.
L352 – Need to explain the significance of the single dorsal fin and Coccosteus here. Sentence is unclear.
L357 – Need to define macruriform
L374 – Should be “ … kind of approach can be …”
L376 – Should be “ … in order to make inferences about …”
L379 – Should be “…sensitive to convergence…”
L384 – Should be “ … us to know what some of the first vertebrates…”. However, placoderms are far far from the first vertebrates, so I would reconsider this sentence.
L388 – The closing remarks are a little long and repetitive, I would consider rewriting these.

•	Intro & background to show context. Literature well referenced & relevant.
L66 – would be beneficial to include a date with reference here
L76 – again, include a date and reference here
L291 – explain what Orodus is, a smaller fish?
Aside from these minor points, I think more emphasis needs to be placed on the controls on morphology. Function is mentioned but not discussed in detail. The relationship between jaw size and ecology again is not discussed. So I feel that there needs to be a more comprehensive introduction to the theory. E.g. why do fast cruising sharks have the tails they do?

•	Structure conforms to PeerJ standards, discipline norm, or improved for clarity.
Yes. But please see notes above.
•	Figures are relevant, high quality, well labelled & described.
Yes.
Experimental design: •	 Original primary research within Scope of the journal.
This article provides a good framework for the estimation of Dunkleosteus size; a large and iconic fish. However, the sole comparison with the great white jaws is not justified adequately in text.
•	Research question well defined, relevant & meaningful. It is stated how the research fills an identified knowledge gap.
The research question is well-defined and relevant for the estimation of fossil fish body size. However ecological correlates are neglected, which are an important part of the study.

•	Rigorous investigation performed to a high technical & ethical standard.
In essence this is a statistical approach to reconstructing Dunkleosteus postcrania. While competent, there is little ecological justification presented to support the findings, and I feel a more the problem deserves a more thorough approach.

•	Methods described with sufficient detail & information to replicate.
L145 – Might be beneficial to explain what the pinnochio effect is here or in the introduction.
L149 – unclear as to why you are using 33 white sharks, and not all shark species here. Is there evidence for a direct comparison with a single species?
L205 – Should be “… structure involved in thrust generation …”

•	Raw data supplied (see PeerJ policy).
Yes. Plots in Supplementary data 3 may need axis labels or for clarity. Crosses and circles need to be explained.
Validity of the findings: Impact and novelty not assessed. Negative/inconclusive results accepted. Meaningful replication encouraged where rationale & benefit to literature is clearly stated.

•	Data is robust, statistically sound, & controlled.
While an impressive array of statistical tests have been utilised, I do not believe enough justification has been provided for the comparison of Dunkleosteus with the great white shark. This justification is a very important part of the analysis, since the authors themselves state the variability of morphology based on ecological and functional factors. For the comparison to be valid, I would need to see more evidence that the feeding mode and locomotion style of the two were very similar.  The alternative is to run a similar analysis of other sharks of similar size (e.g. whale sharks, basking sharks, Greenland shark etc) to show a universal trend separated from ecology.
Secondly, the predictive power of this technique is stated on numerous occasions (e.g. L323); however the authors have not applied it to modern sharks to test this. E.g. Does the regression predict the size of a whale shark based on jaws?

•	Conclusions are well stated, linked to original research question & limited to supporting results.
L268 – Needs a reference
Otherwise the links to original research are good.

Conclusion is a little repetitive, which reflects the limited scope of the investigation. This is not necessarily a bad thing.

•	Speculation is welcome, but should be identified as such.
Speculation is separated from fact well.
Additional comments: This is a competent statistical comparison of Dunkleosteus with modern sharks. The question is not novel, but the approach used here is for this species.

I like this paper a lot, and it deserving of publication, but not in its current form. The comparison of jaws with only the great white shark is not justified or explained in text. The regression used to predict body size or tail type in an extinct animal is not tested here on modern sharks. Were the authors to choose a large pelagic plankton-feeding shark and predict tail span, this may go some way to testing the validity of their 'comparative framework'.


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: ECOMORPHOLOGICAL INFERENCES IN EARLY VERTEBRATES: RECONSTRUCTING DUNKLEOSTEUS TERRELLI (ARTHRODIRA, PLACODERMI) CAUDAL FIN FROM PALAEOECOLOGICAL DATA
Review round: 1
Reviewer: 3

Output:
Basic reporting: This is a really clever study which seeks to reconstruct the unknown body shape and size of a large, extinction charismatic megafauna (Dunkleosteus) using inference from living analogues among the sharks through the inference of general rules for fish body form. However, this worthy effort has a number of important issues which reduce the strength of the arguments and the ability to infer the morphology of extinct fishes with high probability; These need to be resolved before publication. It requires better organization, stronger justification of specific assumptions and arguments, and reconsideration of the methods.
Experimental design: Comparison of sharks and placoderms: I can see the basic logic for comparing Dunkleosteus exclusively with living sharks. Dunkleosteus is a large, generalist predator with sharp-edged jaws found in an open water setting, so modern great whites and other sharks are likely the best modern analogues. However, this argument is not explicit in the paper, nor is the case for selecting actively pelagic sharks as the group with the right body shape and proportions made clear. There needs to be a real comparison of the head and jaws and head size of Dunkleosteus and sharks to determine which shark ecological group is the ideal analogue. Reliance on past speculation is not enough.
	Shark morphospace analysis and results: The results of the morphospace analysis are a bit muddled - there's quite a lot of overlap between sharks with different ecologies near the center of PC1 and along most of PC2. How do we know Dunkleosteus exhibited a morphology matching that of active pelagic sharks at their most distinct (e.g. the 4 with the most negative scores on PC1) and not at their most generalist (the other 6 points)? It is possible the restricted set of landmarks artificially increased the degree of overlap between different shark ecological groups. Why was body depth/shape and first dorsal fin position/form not captured by the landmark set? These aspects also vary in sharks, are important aspects of fish form related to locomotion and ecology, and are unknown in Dunkleosteus. Indeed, the body depth of the Dunkleosteus reconstruction in Fig. 4B is much greater than that of the sharks used as as analogues for inferring its body size and caudal shape, and the dorsal fin is unlike that of known large, pelagic fishes. It would be better to base all aspects of the body on quantitative inference. It is also not clear whether caudal fin edge shape, another ecologically relevant trait, was recorded, as the landmark sets in Fig. 1A and 1B disagree.
	Dunkleosteus life-mode: This paper also needs more explicit justification for why Dunkleosteus was likely to be an active pelagic, "body and caudal fin"-type continuous swimmer than just citing Denison and Carr, and more shark-like than teleost-like. Some of the required evidence is referenced throughout the discussion (e.g. sedimentological evidence; the paragraph from 283-302 which should be moved forward) but not elucidated up front. A large range might be evidence, but body and caudal fin swimming, and continuous swimming, are not required for such (see the spread of Indo-Pacific reef fishes, for example).
	Inference of body length: It is not clear why body length was estimated only from great white sharks. Are body length/jaw length ratios already known to be more dependent on ecomorphology across sharks, or fishes, than ancestry? While an argument is made for not estimating size based on smaller arthrodires, would it not be more appropriate to apply the shark scaling formula to placoderm relationships than assume the same relationship as in one species of shark?
Validity of the findings: Dunkleosteus reconstruction: While it is likely that Dunkleosteus did have a caudal form resembling that of modern pelagic sharks given what we know about fish ecomorphology, the arguments in the paper are not yet strong enough to support this assumption as laid out above. In addition, the new reconstruction of Dunkleosteus may have a correct tail, but the body depth, and other fin forms are still based on Coccosteus, which the authors clearly argue is not a good analogue. A full attempt to infer the form of early vertebrates requires consideration of these ecologically important aspects as well. An improved landmark set for sharks would go a long way to resolving this.
Additional comments: line 72: "pteraspidimorphs"

193: "hypocercal"

269: Appalachian Basin, Tafilalt Basin

280: thunniform

285: Lamsdell and Braddy 2009 did not explicitly test the trophic position of Dunkleosteus.

360: This section seems unnecessary. Paleoart should be based on the most up to date reconstructions as a matter of course and good paleoartists know this.

Fig. 1 The landmark sets in Fig. 1A and 1B disagree.

Fig. 4A It is not clear from the paper where these outlines come from.

Fig. 4B The reconstruction Dunkleosteus has much greater body depth than the sharks which provided the inferred caudal fin shape. Why is this assumed? Also, why are the median and paired fins assumed to be more like Coccosteus than pelagic sharks, since the shapes of these are also related to locomotion?


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 CDK1 PHOSPHOMIMIC MUTANT OF MCAK IMPAIRS MICROTUBULE END RECOGNITION
Review round: 1
Reviewer: 1

Output:
Basic reporting: The microtubule depolymerizing kinesin-13, MCAK, plays critical roles in spindle assembly and in correcting improper kinetochore attachments.  Because MCAK is a potent depolymerase, its activity is spatially and temporally regulated, but the mechanism of this regulation is not well understood. In the current paper the authors perform a thorough characterization of a T537 phosphomimic mutation of MCAK that lies in the catalytic domain of MCAK and which has been shown to be phosphorylated by Cdk1.  They report that the T537E mutation results in decreased microtubule depolymerization activity due to its inability to remain at microtubule ends.  This finding is a logical extension of their previous work in which they showed that mutation of highly conserved residues in alpha-helix 4 of MCAK also resulted in reduced microtubule depolymerization activity and a reduced binding to microtubule ends.  Because T537 lies is positioned adjacent to alpha-helix 4, the current work provides strong corroborating evidence that this region is critical for recognition of microtubule ends and is an ideal way to modulate MCAK activity.

•	The data presented is short, sweet, and to the point.  The text is clearly written, and the presentation of the data makes it easy for the reader.
•	The data is put in the context of the field, but the authors may have missed an opportunity to discuss the broader mechanisms of regulation of MCAK activity, discussed in more detail in point 3 below.
•	It would be helpful to the reader if the authors reported what is plotted.  For example, 1B represents a box and whiskers plot and 1C represents mean +/-???.  The box and whisker definitions nor the error bar values (SD or SEM) are presented to the reader.
•	For the original data supporting Fig. 1C, there is only one set of data for the +tubulin and +microtubule samples, and yet the Table says that n=3.  Please clarify.
•	In Fig. 2A, please provide the colors on the kymographs to the reader either on the figure or in the legend.
•	For Fig. 2C and 2D, it would be helpful to the reader if the authors reported the fit of the data in the graph so that the reader does not have to go back and to the table.  This is also true for Fig. S2.  In addition, for each of these data sets, the excel sheet only has one set of data, and yet the tables say n=3.  Since the data appear to be normalized, is it not possible to plot the average +/- SD of the normalized data in the graph?  This would present all of the data to the reader.
Experimental design: •	This is a well-done characterization of a mutant form of MCAK.  The data provide a potential mechanistic understanding of how phosphorylation may regulate the catalytic function of MCAK.
•	This is the first detailed biochemical characterization of a regulatory phosphorylation that occurs in the catalytic domain.
•	All experiments appear technically sound with sufficient replicates.
•	The methods are well-described.
Validity of the findings: •	The results are clear, and the differences between wild type and mutant are clear and robust.
•	The conclusions of the study are valid and well-justified.
Additional comments: •	In the models discussed at the end of the paper, the authors are not taking into account the multitude of observations showing that the other domains of MCAK target it to the kinetochore, inner centromere, spindle poles, or plus-tips of microtubules.  Therefore, MCAK may be positioned near the microtubule end, so the key event is likely the residence time with the curved tubulin not just being at the end.
•	It has also been well-established that MCAK’s microtubule depolymerization activity requires the positively charged neck region in addition to the catalytic domain.  The neck is also the site of a critical Aurora A/B phosphorylation site, which has been shown to regulate microtubule depolymerization activity.  Both the Wordeman Lab and the Walczak Lab have done extensive mechanistic analysis of how the neck and the regulatory phosphorylations affect MCAK activity.  It would be helpful to the reader if the authors included some of this work in the discussion.  For example, Ovechkina et al, 2002; Moore et al, 2004; Wagenbach et al, 2008; Cooper et al, 2010; Ems-McClung et al, 2013.