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: EARLY LANGUAGE COMPETENCE, BUT NOT GENERAL COGNITIVE ABILITY, PREDICTS CHILDREN’S RECOGNITION OF EMOTION FROM FACIAL AND VOCAL CUES
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript tackles the association between language difficulties and emotion recognition using an existing longitudinal dataset. The introduction provides a concise and relevant background. The following comments may be useful for the authors to consider:

Introduction

-	Line56: One hypothesis has been posed – “In the current study, we test the hypothesis that language supports development of accurate emotion identification by studying a population that have reduced opportunity to learn about emotion concepts through language”. However, the results speak to three key questions:
1.	Does early language competence predict later emotion recognition?
2.	Do children with DLD have poorer emotion recognition skills than their peers with typical language?
3.	Do children with DLD make similar errors in emotion recognition tasks to their peers with typical language?

It may be useful to the reader to include more specific hypotheses in the introduction?

-	Have there been any systematic reviews or meta-analyses on the association? This would shed light on the reliability of this potential association.

Article structure
-	The manuscript was well structured and easy to follow
-	Methods section could benefit from additional sub-headings for inclusion and exclusion criteria (see comments below)

Table 1
-	Is there a reason for reporting age in “months”? I think this makes sense for young children (< 4 y/o), but is harder to conceptualise for older children. Perhaps consider reporting age in years?
-	May be more common to report N for sex rather than percentage
-	The test scores reported in the table do not match the test descriptors included in the methods section – what is the language composite?
Experimental design: This research is within the Aims and Scope of PeerJ. It tackles an interesting research question and provides a step towards enhancing our body of knowledge on the relationship between language difficulties and emotional processing. However, I have the following minor comments that could improve the overall quality of the paper:

Materials and Methods
Sample description
-	It would be helpful to have more information about the DLD group earlier – rather than in the results
-	The NPS group took me by surprise, and I was unsure of the relevance of this group in relation to DND. Perhaps justify this further and earlier?
-	Perhaps include the cut off criteria for the CCC-S?
-	Line 114: consider re-warding “in in-depth”
-	The inclusion and exclusion criteria need to be clearer. Perhaps consider separate subheadings to delineate these criteria?
-	Line 119: Can you include details on length of the assessment, location, and how the assessment was conducted?
-	Clarify the diagnostic criteria used to classify DLD children – especially considering that this is a perceived strength of the study.
-	It would be helpful to clarify the criteria used to classify intellectual disability
-	Line 129: state the additional “associated conditions” other than autism

Consent
-	Line 133: Rephrase the (in where the study started)
-	Line 134: UCL – not previously defined

Assessment procedure
-	It would be helpful to have information on the skills that are being measured rather than the tests that are used. For example, what subtests from the ACE are being used, and what language skill does this measure? It would also be helpful to include more information on the reliability and validity of the tests (given the heterogeneity in assessing language difficulties) as well as state the cut-off scores used to indicate DLD.
-	Line 154: reference for SASOT E32 is needed
-	In the discussion, you refer to DSM diagnostic criteria for DLD. However, this criteria is not used in your methods section to justify group sections. I would recommend integrating DSM criteria into your selection criteria, or removing this section of the discussion

Year 6 Emotion regulation task
-	This section was difficult to follow and the expression of this paragraph could be improved – particularly Lines 172 – 178. Could you present the paradigm and/or stimuli visually?
-	Line 170: Is there evidence for this task being used with children?
-	Line 171: What type of developmental disorders has this task been used in with adults (Jones et al., 2011).

Sampling weights and missing data
-	You propose a model that might predict inclusion of the sample. Can the authors please justify the proposed variables? Definitions are also needed for certain variables – CCC-2 score is included but what is this a measure of? Is it the Castles and Coltheart Reading Test? And if so, why would reading predict inclusion in the sample? As is SDQ – strengths and difficulties questionnaire? Why would internalising and externalising difficulties predict sample of included participants?
Validity of the findings: The use of an existing longitudinal database to analyse the association between DLD and emotion recognition adds to our existing knowledge base of this association.  The data has been provided and the study has been pre-registered. The following comments could also be considered:
-	Remove interpretation of findings from the results section to the discussion
-	Is there any data on emotion recognition in Year 1? Or language at Year 6? This would be useful information in terms of the direction of association.
-	Consider investigating association between language and poor mental health (using SDQ data) if available – this is mentioned in your discussion and would be interesting to investigate – although perhaps not for the purpose of this manuscript!

Discussion:
-	Line 300: Evidence for a positive or negative moderate relationship? Relationship seems to imply causation (to me) – perhaps “association” would be a more accurate term?
-	The discussion would be strengthened with further critique and comparison of the findings against previous literature.
-	Line 311-312: Not entirely true regarding N < 20 sample size of previous literature. perhaps reference the studies that support your argument?
-	Line 313-314: Specific reference to DSM criteria for DLD that has not been mentioned as selection criteria. Please address this point
-	Line 322: What makes this the “best” evidence? This line needs work – particularly in regard to the claim that emotion recognition deficits are “directly linked to language proficiency” – the results do not speak to direct links. The authors should be more tentative with this conclusion.
-	To add weight to argument that poor language is associated with poor emotion recognition and poor mental health – you could look at associations with emotional health problems as you included SDQ as a variable?
Additional comments: Thank you for the opportunity to review this manuscript. I wish you all the best for your future endeavours!


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: EARLY LANGUAGE COMPETENCE, BUT NOT GENERAL COGNITIVE ABILITY, PREDICTS CHILDREN’S RECOGNITION OF EMOTION FROM FACIAL AND VOCAL CUES
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: The research question is relevant and meaningful. The method and design are clear, appropriate, and well described. I believe that in the emotion recognition task, the facial expressions were of adults and adults produced the non-verbal sound stimuli.  I think it would be helpful for the authors to explicitly indicate this.

There is one thing I was a bit puzzled about. In the Assessment procedure section, Year 1 language, the authors indicated that they created a single language composite score by averaging the Z-scores.  In the Analysis plan, standardization of scores section, the authors note that they standardized the six language assessments and the two NVIQ assessments using the LMS method.  Can the authors clarify how the Z-scores are related to the standardization?
Validity of the findings: The findings represent an important addition to the literature and are clearly reported.  I think it would provide additional clarity, however, if the correlations among the variables included in the path analyses were reported.  The authors provide the correlation between the two outcome variables but nothing else.  I think Table 1 would be improved if the Full sample descriptives were removed since the language groups are of primary interest.

The Discussion provides a well-synthesized interpretation of the findings within the context of previous literature.  The authors acknowledge study limitations; however, I think the authors could also acknowledge that there might be other factors that contribute to emotion recognition skill (e.g., mother-child discourse about emotions) that were not included in their study.
Additional comments: No additional comments


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

Input:
Title: EARLY LANGUAGE COMPETENCE, BUT NOT GENERAL COGNITIVE ABILITY, PREDICTS CHILDREN’S RECOGNITION OF EMOTION FROM FACIAL AND VOCAL CUES
Review round: 1
Reviewer: 3

Output:
Basic reporting: This paper is concerned with an interesting aspect of DLD and its implications for the social-emotional well-being of affected children. The paper is generally well-written (see some copy-editing issues below) and describes a carefully-executed study that will be of interest to DLD researchers and clinicians alike. My comments and suggestions below are offered as ways of further strengthening the MS, particularly in relation to placing it in a slightly broader context of work that has gone before in the emotion recognition space.
1.	In the introduction/lit review, I suggest providing coverage of the work of Brinton and Fujiki and colleagues, as their work is important to the question of emotion recognition in children with language difficultes, for example this paper:
Brinton, B., Spackman, M. P., Fujiki, M., & Ricks, J. (2007). What should Chris say? The ability of children with specific language impairment to recognize the need to dissemble emotions in social situations. Journal of Speech, Language, and Hearing Research 50(3), 798-811.
2.	There is also a body of literature on alexithymia which seems relevant to bring in either in the introduction or the discussion (or both). While I hesitate to reference my own work in reviews, my colleagues and I described high rates of alexithymia in a sample of young offenders a few years ago. Although we did not find its presence correlated with language profiles, we did report it as a significant comorbidity with LD and this seems important in relation to the links between language skills and mental health problems in vulnerable children and adolescents. It is definitely relevant to the provision of support services to children and adolescents with LD. The citation for this work is as follows:
Snow, P.C., Woodward, M., Mathis, M. & Powell, M.B. (2015). Language functioning, mental health and alexithymia in incarcerated young offenders. International Journal of Speech-Language Pathology, 18(1), 20-31. DOI: 10.3109/17549507.2015.1081291.
3.	In the initial description of the current study, p. 3 of intro, line 93, reference is made to “…a large number of children with DLD” however it is not possible to discern here what is meant by the term “large” – does this mean for example, that it was an unusually disproportionate subgroup?
Experimental design: The design is appropriate to the questions examined.
In the Method, under the heading Year 6 emotion recognition - line 175 – it is not clear what the nature of the response was that was required by children, but it is implied further down on the same page (line 184) that it was not verbal. This requires clarification.
Validity of the findings: Discussion
a.	It would be helpful to comment on the implications, if any of the findings for the Theory of Constructed Emotion that was introduced in the opening to the paper.
b.	As noted above, I see clear links in the findings of this study to the literature on alexithymia and would really like to see that brought in to the Discussion. This construct also has implications for the ability of children with LD to engage in counselling, which often has a focus on identifying, discussing and re-framing affective distress – all of which of course is done verbally.
c.	While I agree with the possibility that interventions aimed at improving language skills MAY result in improvements in emotional recognition, I think we need to be careful not to over-burden the intervention field too much – it is difficult enough to establish efficacy and effectiveness on the proximal skill set, let alone generalisation to a more distal skill-set such as emotion recognition. Perhaps this could be framed a little more speculatively.
d.	It would be helpful in the Discussion to provide some consideration of the fact that correlations were not established between emotion recognition and age.
Additional comments: Grammar/copy-editing/expression clarity issues
1.	A few instances of poor subject-verb agreement are noted in the paper, e.g., line 57 in the second page of the intro: population  has; in the Method, line 169 set  has.
2.	On the same page, line 71 – consider substituting “different” for “contradictory”
3.	On the third page of the intro, line 82, the word “emotional” is repeated.
4.	In the Method, line 117 – it is usual to use words rather than numerals at the start of the sentence (depending of course on journal conventions). This occurs elsewhere in the MS also.
5.	On the same page as point 4 above, line 121 – add “criteria” after “DLD”.
6.	Second page of method, line 124 - I suggest adding “probable” before “intellectual disability” and in line 125, adding “below the mean” at the end of the sentence.
7.	Same page as point 6 above, line 133 – remove “in” within brackets.
8.	Still on the same page, line 139 – as a Latin phrase “a priori” would normally be italicised. This occurs elsewhere also.
9.	Method (under heading sample size and power calculations) – line 146 – change “suggest” to “suggested” and remove “a” after “detect”.
10.	Same page as above, line 156 – “z-scores” is normally all lower case.
11.	Still on the same page, line 158 – change “test” to “tests.
12.	In the Method, above the heading “Analysis plan” (line 185) – I am not a fan of “inputted” – could this be changed to “submitted” or similar? Also there is a missing “to” before “give” in this same sentence.
13.	In Method, para above heading “Sampling weights and missing data”, line 190 – change “coverts” to converts.
14.	Same page as above, line 198 – monolingual is one word (no hyphen)
15.	Same page as above – some form of inclusion/includes/ included is used four times between lines 206 and 208.
16.	On the next page, line 212 – change predict to predicted.
17.	Same page as above, change “pervious” to previous.
18.	Same page as above, line 229 – the singular form is criterion (“criteria” is plural).
19.	On the page with the heading “Results” it is not clear why there is a heading immediately under this “Participants”
20.	On this same page, line 239 – add “who” after “participants”.
21.	Final page of Results, line 293 – change surprised to surprise.
22.	Discussion, third page, line 335 – insert “task” after emotion labelling.
23.	My personal preference is to use lower-case n not N when describing sample size, but the authors should check the journal requirements on that.
24.	Where DSM is mentioned in the Discussion, this needs an edition and a reference, as well as a citation in the Reference List.


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: ANALYZING BACTERIAL COMMUNITY IN PIT MUD OF YIBIN BAIJIU IN CHINA USING HIGH THROUGHPUT SEQUENCING
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Chen et al. reported the bacterial community in pit mud of Yibin Baijiu by high throughput sequencing. They analyzed 68 samples from 13 baijiu enterprises with two kinds of samples types consisting of middle layer and substrate layer. And the results are easily to predict, and the author should dig deeply based on the data from HTS.
The following questions should be concerned.
1. Line 25 and the whole manuscript, the 16S rRNA high throughput sequencing is not a correct description, and it should be 16S rDNA high throughput sequencing. The author should correct them and the associated description carefully.
2. The author should pay more attention at manuscript writing, such as: Line 97 the “sterilized bas” should be “sterilized bags”; Line 159: “indices was” should be “were”.
3. Can the author explain what are middle layer and substrate layer (the author can draw a picture to make it easier to know), and why the sample numbers are not the same between middle layer (37) and substrate layer (31)?
4. I think the Table 1 should not be shown in manuscript, and it can be replaced by Table S1. The sd values of Table 1 are too big, which means that analyzing the 13 baijiu enterprises in a whole is not correct, and it should be listed as Table S1.
5. Line 253, “Among baijiu PM of several aroma types, Lactobacillus was a dominant genus”, the author should give a reference.
6. Line 260-261. “Therefore, as a unique dominant genus of “Yibin Baijiu” PM, we speculated that Gelria may contribute to the formation of unique flavour of “Yibin Baijiu”.” The author speculated that Gelria may contribute to the formation of unique flavour of Yibin Baijiu, and I have a different opinion that Gelria may contribute to the formation of humics acid according to Fig. 6.
7. I even do not know what is the aim of this manuscript.
a. According to the Introduction from line 79 to 89, it seems that the author wants to investigate many enterprises that produce CSAB, and find something interesting. However, the author only investigated enterprises in Yibin city, and I think the author should investigate enterprises that produce CSAB in China. Because the 13 baijiu enterprises in Yibin city are too close in distance.
b. At the same time, the author sampled in middle layer and substrate layer of the PM, and the difference between middle layer and substrate layer was not analyzed with the variation of baijiu enterprise. The author compared the two groups in a whole not in every baijiu enterprise. Therefore, there is no difference between the two groups. I think the author should deeply analyze the data they got from HTS.
c. The author focused on the PM of Chines strong-aroma baijiu (CSAB) in introduction. however, the author discussed a lot of other aroma types PM at line 239-251.


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: ANALYZING BACTERIAL COMMUNITY IN PIT MUD OF YIBIN BAIJIU IN CHINA USING HIGH THROUGHPUT SEQUENCING
Review round: 1
Reviewer: 2

Output:
Basic reporting: The presented article concerns the analysis of a popular liqueur from China. This is a traditional drink that has already been analyzed in many ways.
The text is interesting but requires thorough corrections.
An introduction does not explain the purpose of the study sufficiently and should be written in more academic style. The text should go through language correction. Examples:  L97: sterilized bas (?), L148: Rarefaction curves was (?), "origined" or "orginated"  etc.
Experimental design: Methods are used correctly, but I have some comments:
1. Physicochemical properties were performed according to AOAC ?
2. In methodology are added websites links, pleas edit it in a different way
3. Which statistical test was used? In discussion is a piece of information about "t-test" is this "Student's t-test"?
Validity of the findings: The topic is new, but the results obtained describe a liqueur from a specific region. There is no justification in the text of a stronger need for such research. Conclusions are clear and well described.
Additional comments: The text should be language-checked. The methodology should be revised to incorporate the comments. The need for stronger justification for the research.


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: ANALYZING BACTERIAL COMMUNITY IN PIT MUD OF YIBIN BAIJIU IN CHINA USING HIGH THROUGHPUT SEQUENCING
Review round: 1
Reviewer: 3

Output:
Basic reporting: The whole manuscript was basically clear and English is generally good. But the authors should give more description on the defined comprise of fermentation pits in 13 baijiu enterprises, Is there something substentially different in thefermentation pits for the four types of aroma types？
Experimental design: The research questions is clear.
Validity of the findings: The results are clearly stated.
Additional comments: I think the manuscript submitted by Chen et al. descrbied the bacterial community in pit mud of Yibin Baijiu in China by high throughput sequencing. the bacterial community from 68 samples 13 baijiu enterprises in Yibin was analyzed and its correlation with environmental factors.
1. In the introduction section, authors should give more description on the defined comprise of fermentation pits in 13 baijiu enterprises.
2. In table 3, why the author bring the strong-aroma out.
Some minor modifications need to be made:
16S not 16s; Table 1 mg/100g, please leave a space between the number and unit.  P for the significance should be italic.


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: LONG-TERM OUTCOMES OF REPAIRED AND UNREPAIRED TRUNCUS ARTERIOSUS: 20-YEAR, SINGLE-CENTER EXPERIENCE IN THAILAND
Review round: 1
Reviewer: 1

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


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

Input:
Title: LONG-TERM OUTCOMES OF REPAIRED AND UNREPAIRED TRUNCUS ARTERIOSUS: 20-YEAR, SINGLE-CENTER EXPERIENCE IN THAILAND
Review round: 1
Reviewer: 2

Output:
Basic reporting: In this paper Dangrungroi et al. presented their 20 year experience with truncus arteriosus (TA) repair and also long-term outcome of the unrepaired patients. This is an outcome study. The authors could be congratulated that the hospital mortality has dropped from the 50 % (according to their previous reports) to the 30.8 % in the current era.
The paper was written in clear academic English, it is well organised in terms of reading it through. The references are also well organised and are relevant. Most of the figures and tables are well structured, the only issue that I have found was in the Table 4. Mainly, they should have included the number of patients in each category (e.g prenatal diagnosis in 20 out of 52 patients).  There are also some minor errors regarding presenting data (e.g.Table 2; Surgical era 1999-2006 instead of operation in 1999-2006, however they  do not distort meaning. The raw data that authors collected is robust.
Experimental design: In terms of experimental design, the finding of the paper is not completely in line with its aims. In abstract the authors stated that their aim was as follow: “In this report, we aim to report on the survival of patients with TA in our medical center in the recent era”(lines 35-36). However, in conclusion they reported on functional status and then on decreased mortality risk (lines 54-55). I suspect they wanted to say about early mortality as they define previously (lines 114-116), but not on mortality risks. Also, they did not aim to report on risk factors, though they reported on them in conclusion (line 56).
 I also suspect the multivariate analysis by Cox regression is meaningless, as the authors did not provide the number of events in each category (Table 4), and also considering overall small group (n=52), the number of events could not be more than 10 in each category.
Validity of the findings: With regards to novelty in the field of cardiac surgery this paper does not contribute much. The main problems are as follows:
1.	The quoted “crude-for simple and complex TA” hospital mortality of 30.8 %. However, the current hospital mortality is within 5 % and 17.5 % (line 270).  Moreover, the complex TA accounted to 9.6 % (5/52) of patients, so such high number of hospital mortality are not in line with worldwide numbers. The authors also have not provided the hospital mortality for the complex TA.
2.	The comparison of survival between operated and non-operated groups is without sense (lines 213-215). By definition, unrepaired TA leads to early death (most of unrepaired patients died by one year of life( line 342) and those who “survive” are profoundly disable due to Eisenmenger complex. Relatively old age in the group of unrepaired patients could be explained  by lack of early diagnosis (Table 1; the age of suspicion of 0.07 years versus the age of admission to the cardiac center of 1.8 years in the group of unrepaired patients. That means that most of the patients were lost and probably died.
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: LONG-TERM OUTCOMES OF REPAIRED AND UNREPAIRED TRUNCUS ARTERIOSUS: 20-YEAR, SINGLE-CENTER EXPERIENCE IN THAILAND
Review round: 2
Reviewer: 1

Output:
Basic reporting: I think the revision stratified the previous comments. The manuscript can be published with some minor revision.
Experimental design: NO COMMENTS
Validity of the findings: NO COMMENTS
Additional comments: a Please delete the description for the definition of TA in the Introduction section,
b  Is Siriraj Hospital the only heart center which can offer the service for the patients with TA in Thailand? If not, please delete the first sentence in the 2nd paragraph.
c  Please indicate  whether the targeted advance PAH therapy is utilized for the TA patients with or without surgical treatment, because such a therapy could improve the prognosis of the patients with PAH.


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: HIGH TYPE I COLLAGEN DENSITY FAILS TO INCREASE BREAST CANCER STEM CELL PHENOTYPE
Review round: 1
Reviewer: 1

Output:
Basic reporting: Overall, this paper was written with clear English and enough background. However, the points following should be improved.

1. Where is the statement about Figure 1 in the main text? Please include it.
2. Figure 7: You should include low images for the analysis.
Experimental design: Questions, hypothesis and approach were appropriate. However, several points about experimental design, statement, and drawing in the text should be improved.

1. Lines 90-105 and Figure 1: In Figure 1, the gels look floating. Did you use floating gels or attached gels on the dish in your experiments? You should state which gels you used and draw the clear figures.

2. Lines 174-182, 226-234: You should mention how long you cultured the cells on 2D or in 3D conditions “before” you re-seed the cells on the 2D dishes/wells.

3. Figure 4A: You should clearly divide the upper blot set and the lower blot set for avoiding the confusion. I can see very “narrow” space between the blot of YAP and b-actin, however, it is tough to find the space at the first glance. Some reader may think there are two “b-actin” controls in the same blot set.
Validity of the findings: Most of the data and explanation looks fine, however, several points should be improved.

1. Lines 110-112: You used collagenases for digesting collagen gels. Did you investigate the effects of collagenases on the expression of surface proteins, such as CD44? If no, you should perform an experiment to compare the expression of CD44 in the breast cancer cells on 2D dish with or without collagenase treatment.

2. Lines 147: You used only GAPDH for the housekeeping control for qPCR. You should use at least two housekeeping control targets (e.g., b-actin, a-tubulin, S18) for the experiment because if GAPDH is regulated by collagen density, GAPDH is not a good control.

3. Lines 301-302: There are possibility that not 3D condition but 2D condition increased CSC-related genes in breast cancer cells. On the other hand, collagen itself may be critical for the expression of CSC-related genes. To investigate whether collagen itself is critical for the expression of CSC-related genes in your experimental system, you should perform the experiment to compare CSC-related genes in breast cancer cells on 2D culture plates with or without collagen I coating.

4. Lines 358-377: Why you investigated the expression of E-cadherin and ERalpha? You should mention the reason and background why you included these data in this paper before showing the results.

5. Figure 4, Figure 10: You should use at least two housekeeping control targets (e.g. GAPDH, a-tubulin, histone-H3).

6. In Discussion part, generally the conclusions are stated too much without enough evidence. You should use “may” “indicate” “suggest” for the speculation (for example, lines 425-427).

7. Lines 388-389: In your data in Figure 2, in MDA-MB-231 cells, CD44+CD24- cells were increased in HD condition. You should state the results correctly.
Additional comments: The authors investigated whether high collagen I density affects the stemness in breast cancer cells. Although most data was not positive thus the authors concluded that there is no difference of stemness between breast cancer cells in high and low density collagen gels, most of the experimental data was reliable. However, several points about statement, explanation of the experiments, and data itself were not sufficient. In addition, in Discussion part, several statements looks too much. These points should be 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: HIGH TYPE I COLLAGEN DENSITY FAILS TO INCREASE BREAST CANCER STEM CELL PHENOTYPE
Review round: 1
Reviewer: 2

Output:
Basic reporting: In the manuscript entitled: “High type I collagen density fails to increase breast cancer stem cell phenotype”, the authors carefully investigate the stemness phenotype of two human breast cancer cell lines, MDA-MB-231 and MCF-7 cells, in response to culture in increasing collagen density. While the authors conclude that collagen density is not sufficient to fully develop the BCSC phenotype, the work is rigorous, the manuscript is well written and worthy of publication in PeerJ.
Experimental design: Minor points:
1. The graphic representation of culture conditions was very helpful.  With respect to collagen gel culture, the methods section states “Col-I final mixture (175μl) was added to wells of 24-well culture plates (Corning, USA) and placed in the CO2 incubator for 1 hour to polymerize. Col-I gels were then covered with the appropriate cell culture media.”. To this reviewer, that means that the gels remained attached to the bottom of the 24-well plate, which is inconsistent with the graphic in Figure 1. Please reconcile figure 1 with the written methods.

2. As a follow up to comment #1, the authors point out “Col-I gel architecture is affected by factors such as cell culture media, gel thickness, and cell presence, while cell morphology also changes in response to Col-I density”. Restraining the collagen gels by leaving them attached to the bottom of the dish can also influence cellular mechanical signaling and collagen reorganization in response to cellular contractility (Wozniak et al., JCB 2003). Thus, if the gels are attached to the bottom of the dish it is possible that the cells sense a stiff matrix under all collagen concentrations. This may partially explain the lack of collagen fiber reorganization. Perhaps this point can be added to the discussion.
Validity of the findings: This is an relevant and important area of research that will be a benefit to the literature. It is still worth while to note that collagen density may impact CSC markers in primary cell  within the native tumor microenvironment.  It is quite possible that these well established cell lines no longer have the plasticity to aquire markers associated with the CSC phenotype in response to density.
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: HIGH TYPE I COLLAGEN DENSITY FAILS TO INCREASE BREAST CANCER STEM CELL PHENOTYPE
Review round: 2
Reviewer: 1

Output:
Basic reporting: The revised points look clear.
Experimental design: The revision of the maniscript looks enough.
Validity of the findings: The revision looks fine. Although there are no additional experimental data, the authors found previous experimental results from already published papers.
Additional comments: Now it's suitable for publication in this journal.


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: EXPLORING THE INTERACTIONS AMONG SNARC EFFECT, FINGER COUNTING DIRECTION AND EMBODIED COGNITION
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: As I outline in the comments to the author, the design as it is now is not suited for addressing the experimental question stated by the authors.
Simply - in the light of literature it is not possible to investigate influence of finger counting starting hand on the SNARC effect if only participants starting from their right hand are tested. It is not a variable but a constant then. Moreover, in the literature there are multiple hints of evidence that right-starters do reveal SNARC effect, but it seems that their SNARC is weaker than the SNARC by left-starters. However, testing right starters only does not address the issue.
Validity of the findings: As outlined above and in more detail in the general comments - as for now (no left-starters tested with the SNARC task), the results are hardly conclusive.
Additional comments: First of all, I must say that I served as a reviewer to this manuscript few months ago, when it was submitted to another journal, and rejected after a peer review by the editor. I paste this review below. In the submitted version the authors did not consider any of these points. I still believe these need to be addressed and hardly believe that it is possible to address them without additional experiment (testing left-starters with the SNARC task). However, if the Authors provide good arguments, I can reconsider this opinion.

Below I paste my old review.
-----------
n the paper the authors investigate relationship between SNARC and finger counting routines. In particular, they investigate on how right-to-left finger counting routine relates to the SNARC, trying to disentangle between the Mental Number Line account and the “Manumerical” hypothesis. The research question stated by the authors is valid and theoretically sound. Nevertheless, I have numerous comments and doubts, which I list below. I think they can be addressed within a major revision. However, I am not sure, whether it is possible to handle these comments without additional experiment. If the authors come up with good arguments, that it is not necessary, I can reconsider my viewpoint.

My biggest concern regarding the study spreads from literature coverage and extends to approach taken for data collection, and its interpretation, so I will try to describe my point according to this order.

One of the basic arguments raised by the authors is that methodological differences have led to discrepant results as regards the most prevalent finger counting routine. I generally agree that this can be a point. Actually the authors should also mention that this was empirically demonstrated by Wasner and colleagues (2014, Cognitive Processing). On the other hand, despite obvious methodological differences, I believe there are still some cultural (even within the cultures using the same reading/writing direction) differences in finger counting routines (as the authors themselves report studies from numerous European countries). One might argue that these differences can be due to methodological differences. However, this is not the whole story. There are at least two large-scale studies showing that using the same (even if not ecologically valid) procedure, reveals massive cultural differences in reported finger counting routines. This gets pretty obvious e.g., when one inspects Figure 2 in Lindemann et al. (2014). Proportion of left-starters differs from ca. 85% in the US participants to about 50% in Belgian and Italian participants. Cipora et al (2019, Behavior Research Methods; Supplementary Material, Part 5) also report massive between country differences in finger counting routines. I can hardly understand on how the method validity (if this was the only case) leads to different biases in different cultures.

Another related point here. If the authors wish to discuss the minor methodological differences between studies, which might have led to inconsistencies in results, the review of existing evidence must be done at a more fine-grained level regarding differences between methods. For instance, in study by Hohol and colleagues (2018) participants did not see the questionnaire while asked to count with their fingers, but were asked count with their fingers first, and then were given a questionnaire and asked to mark their responses (this is actually indirectly mentioned in the discussion when the authors write about the validity of the ecological method, but in the introduction it only states that modified version of Fischer’s questionnaire was used). This could differ from a situation if the drawings are constantly visible and participants are only to mark their responses without actual counting.

Here I come to another important point, which refers to the approach taken by the authors. Specifically, only right starters have been tested in Experiment 2 (except two left-starters, who were excluded from the analysis anyway). Testing right-starters only stands in contradiction to the opening paragraph of the Discussion section where the authors argue about independence of the SNARC from finger counting. How this conclusion can be stated if only one group is tested? To test it, right-starters should be compared with left-starters.

The observation by Fischer (2008) that there is no SNARC in right-starters seems not to be a strong enough argument to make investigating only right-starters legitimate. Robust group level SNARC was observed multiple times in cultures, in which vast proportion of individuals are right-starters.

In a recent study Cipora and colleagues (2019; Behavior Research Methods; Supplementary Material Part 2) replicated the difference between right- and left-starters in the SNARC. Nevertheless, despite group difference (effect size was actually very small), the robust SNARC was found in both groups.

In the current study it is impossible to verify it as only right-starters have been tested, and it is hard for me to find (nor think of)  any solid conclusion that can be drawn from the study as it is now. For the same reason, I am also not sure whether the results reported by the authors make it possible to draw such a strong conclusions as regards the nature of the SNARC, as the authors do on upper part of page 19.

Other points:

Introduction:

This section would benefit from streamlining. For quite a long time I cannot follow the logic of the literature review presented by the authors as regards the goals of this literature review.

Maybe information on failure to replicate the crossed hands SNARC should be put next to information on observing the effect. This can be more accessible to the readers. In the context of hand and their position for the SNARC raised in this paper, it would also be worthwhile to mention a study by Viarouge et al. 2014 (QJEP).

Description of Fischer (2008) study is a bit misleading because provided sample size and percentage comes from his Experiment 1, which only showed prevalence of the right- and left-starters. SNARC was evaluated in a subsample of this in Experiment 2.

Hypotheses and Method:

The authors build rather elaborate prediction about hand position and its correspondence to actual position of hands of the participants during the experiment. They also do emphasize that they wished to have the hand images as natural as possible. As in principle I see a point in that approach, I have one doubt. Only photos of male hands were used. From studies on immersion in virtual reality one can infer that similarity between own body and the body displayed in VR environment plays a considerable role for the immersion experience. For this reason one could expect different effects for males and females in the study. This issue should be at least mentioned and discussed by the authors.

Results:

A short paragraph / sentence summarizing conclusions of Experiment 1 could be added before moving to Experiment 2.

Experiment 2 – in the part on number presented as hand pictures, the authors are investigating a four-way interaction. The description is fairly hard to follow (see Halford et al., 2005, Psych Science for an evidence that humans have considerable difficulties to mentally process such complex interactions). I would consider streamlining the description and making sure this is accessible to the reader. Maybe a table summary would help? I have no clear solution to that.

What do you mean by exact t-tests? Does it refer to follow-up (post hoc) analyses, or a very specific method in multivariate statistics (e.g., Lauter, 1996)? If it is the latter, please provide a short footnote explaining it, because it is not a commonly used method.

Discussion:

This section would also benefit from streamlining, and in principle I think that multiple changes need to be implemented as a consequence of considering the above arguments.

p 18 last part is framed as a hypothesis that the measurement method influences the results of finger counting questionnaire. I think this is not a good framing here, the authors have actually not tested that.


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: EXPLORING THE INTERACTIONS AMONG SNARC EFFECT, FINGER COUNTING DIRECTION AND EMBODIED COGNITION
Review round: 1
Reviewer: 2

Output:
Basic reporting: ### Language:
Although I am not a native English speaker myself, I noticed several odd sentences and grammatical errors in the manuscript. The manuscript would profit from proof reading by a native English speaker.
In parts (especially the last section in the introduction (hypotheses exp 2) and the results section of experiment 2) the manuscript is not clearly written. It would be helpful to more explicitly/transparently describe the train of thoughts/reasoning behind certain statements or analyses. Especially in the results section, it is useful to reiterate the hypothesis that is being tested with a specific analysis/mention whether or not the expectations were met when presenting the results. Or – vice versa – describe the expected effect (main effect, interaction) more explicitely in the hypotheses section.

### Literature
The authors give a broad overview of relevant literature. Although the authors present a multitude of studies relating to the one or the other research question, a line of arguments that leads to the respective research questions is hard to filter out for the reader. Put differently, the presentation of previous research is not well structured and the relevance to the study presented is not always clear. The authors should try to make one argument per paragraph (maybe working with subheadings if it helps following the line of arguments) and end a paragraph with the important statement/conclusion of this paragraph for the study at hand. As one example, the in lines 97-152 (that is more than two pages) the authors mix (amongst other things) research on the manumerical hypothesis and findings regarding effects of situatedness on counting directions.

### Figures/Tables
Quality of Figure 1 might have to be checked

### Data
Aggregated data of experiment 2 has been made available (I guess the numbers are inverse efficiency scores but this is not specified in the file). Raw data of experiment 2 are not provided.
Experimental design: ### Research questions
The presented study addresses multiple research questions, of which I think the first two are described clearly in the hypotheses section (1. Assess the proportion of right- and left-starters in an Italian sample, 2. SNARC effect with a restricted stimulus set (Arabic digits)). After this I have a hard time grasping the research question and especially also the justification of hypotheses.
1. “… and to verify the congruency between the finger counting direction (i.e., left hand use for small numbers) and the SNARC effect (i.e., better performance with the left hand for smaller numbers).” I do not understand what the authors are referring to here because in Experiment 2 only right starters were investigated so I don’t see how the authors want to investigate the association of counting direction and the SNARC effect (neither with Arabic digits or hand pictures).

2. “We expected that, according to the SNARC effect, for both codes the performance of participants would be better for smaller/larger numbers categorized with the left/right hand, respectively.” I assume that “code” refers to Arabic digit and hand stimuli (this is not completely clear to me because on the lengthy description that proceeds this hypothesis). If so, the interaction of number x response hand interaction should be present for both Arabic digits and hand stimuli (?)

3. “We also hypothesized that, according to an embodied perspective, the photographs of a left/right hand would lead to a better performance with the corresponding left/right hand used to respond.” Interaction of depicted hand and response hand (?)

4. “Finally, we were also aimed at exploring whether this hand-compatibility effect could be stronger for stimuli presented palm-down (as this was the posture of the participants’ hands during the task) or it was stronger for stimuli presented palm-up (as the viewed hands during a first-person finger counting). Thus our hypothesis was that of a better performance with the left/right hand for smaller/larger magnitudes (SNARC effect) shown by means of left/right hand images (embodied cognition) presented either palm-up (as in first person finger counting) or palm-down (stronger effect of the embodied cognition than perceptual habit).” First, it is unclear if this is an exploratory or a confirmatory analysis. Nevertheless, the hypothesis the authors formulate here is unclear to me.
Validity of the findings: ### Discussion
1. The authors state that “Our results show that the SNARC can be independent of the finger counting habits.” (line 468f), and that “We can conclude that the SNARC effect is based upon a MNL instead of being dependent upon finger counting direction.” (line 473f, see also conclusions drawn in the conclusion section and statement in the abstract). Neither statement is justified because only right-starters were tested. To be able to judge potential influences of counting direction, counting direction needs to be manipulated.

2. Following from the fact that the research questions in experiment 2 are not clearly derived, both the reporting of results and the discussion of these results do not provide a clear picture of what is going on and what it might mean. In the results section, a series of results is reported, partly reiterated in the discussion section and the general message is hard to grasp. I think it is necessary to focus the analyses, tailor them to clearly formulated questions that address a specific gap. Otherwise it remains a list of many results lacking a clear contribution to existing research or prompting further studies.

### Conclusions
Given that a SNARC effect only seems to be present under very specific circumstances with hand stimuli (and was found in an exploratory analysis as I understand) arguing that “The SNARC effect is a pervasive effect which is present not only for Arabic code numerical stimuli, but it is also present when a different code is used, such as finger configurations corresponding to 1-to-5 magnitudes.“ is an overstatement.
Additional comments: ### Other comments
- The authors should check the use of “frame of reference” (line 171 This frame of reference, line 183 object-base frame of reference, line 184 egocentric frame of reference etc.).
- Analysis counting direction and handedness score: This analysis wasn’t introduced in the introduction and is not discussed in the discussion. Also, why make three groups, if there are only 5 people in one group/ why perform an analysis on 5 people?
- Which post hoc test was used? (Duncan, line 334, or Bonferroni, line 427)
- E.g., line 233 (s/he): The singular “they” is a generic third-person singular pronoun in English. Use of the singular “they” is endorsed as part of APA Style because it is inclusive of all people and helps writers avoid making assumptions about gender.


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: EXPLORING THE INTERACTIONS AMONG SNARC EFFECT, FINGER COUNTING DIRECTION AND EMBODIED COGNITION
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment here, but see comments in the section on validity of findings. These comments refer also to this point, but it was really hard to split them.
Experimental design: No comment here, but see comments in the section on validity of findings. These comments refer also to this point, but it was really hard to split them.
Validity of the findings: While reading the revision and responses to the reviews, I think that making it explicit that the right starters are the target sample somehow helps defending the paper as it is now. However, I have a feeling that the “Manumerical hypothesis” as framed by the authors seems to be a little bit a strawman. Specifically, as framed by the authors, the “manumerical hypothesis” claims that finger counting is THE ONLY factor determining the SNARC (not sure whether such understanding will be even shared by M. Fischer, who proposed it). In that case the experiment allows verifying it. As a side note, even in original Fischer’s study, the SNARC in right starters would be significant if tested one-sided (note that one sided tests are actually recommended by several authors in the case of the SNARC effect because there is a clear directional prediction). Moreover, the null result as reported in the paper was probably also due to presence of two participants revealing very positive slopes (> 40).
On the other hand, what the current design does not address is whether the finger counting habits INFLUENCE the SNARC. It can well be, that right-starters reveal weaker SNARC than left-starters. This is what we have actually found in the online study, I mentioned. Please note that, according to Fig 2 in Lindemann (2011, not 2014, sorry for a typo in the previous review), in Italy and Belgium the proportions of left-starters is only about 50%, while multiple SNARC studies come from these countries. Does this mean that the “manumerical hypothesis” holds or not? I think this remains an open question.

Putting aside my personal ideas on which version of the hypothesis is more interesting, I believe, verifying the “bold” version of “manumerical hypothesis” has some value as it is. Therefore, this manuscript provides a nice systematization of evidence present here and there in the literature and adds up some new and interesting data collected with the aim of testing this particular hypothesis. However, it must be clearly stated what the results tell (“bold” version does not hold) and what they do not because of not testing a group of left-starters (i.e., they do not say whether finger counting routines play a role”).

The conclusion that future studies should compare left- and right-starters: this is actually what was done in the online study in a quite large scale. I personally support replication efforts as a way to address several problems of psychology, but the framing as proposed by the authors states that it would be a kind of novel way to pursue the question, which is actually not the case.
Additional comments: Abstract (line 33): there is still a confusing sentence on independence of the SNARC from finger counting habits. Please adjust in line with adjustments in the main text.

Lines 54-55: the description of the SNARC effect is somehow weird. It is a mixture of presenting the effect and (probably) reporting of Experiment 3 from Dehaene et al., 1993. As it is now: “were faster at categorizing smaller numbers (from 0 to 5) with the left hand and larger numbers (from 4 to 9) with the right hand”, the sentence contradicts itself – numbers 4 and 5 are claimed to be responded faster by left and right hand at the same time. I know what you probably meant here but the formulation is not very fortunate.

Section 1.2 – I still found it hard to follow. Would benefit from streamlining and making it clear on why certain information / arguments are provided. Not fully sure about the relevance of the neuro data. It should be more integrated into line of argumentation or skipped.
Not sure why the MARC effect is introduced at this moment and how does it relate to previous argument.
I am not sure what the authors wanted to convey in the first paragraph of this section and how it was meant to relate to the second paragraph.

I am not fully sure whether citation of a work by Schroeder and colleagues (2019) is relevant here. Obviously, being involved in this paper I have no interest in kicking out this citation (rather the contrary), but please mind that this publication is stage 1 registered report, where we outline some theory about the MARC effect justifying the study to be conducted, but no data has been collected yet. If you referred to the theoretical consideration, consider making it explicit.

Line 138. The added text is misleading because it is meant to refer to study by Linemann and colleagues (I guess) but there is no citation and the previously cited work is Wasner and colleagues. As far as I remember, the latter did not consider cross-cultural comparisons (correct me if I am wrong).

“Exact t-test” – I am still not convinced that one-sample t-test is also known as “exact t-test”. Quick googling also did not solve it. Why not sticking to one-sample t-test as it is known in most statistical packages and handbooks? The term one-sample t-test is also quite well-known to SNARC researchers.
Related point – why not comparing two conditions directly but using a mean in one condition as a reference? An analysis as proposed by the authors would make sense to me if: (a) comparison is made to a specific value (e.g., zero), which would have a certain theoretical meaning, (b) one tests a specific group / sample (such as patients or so) against well-established population norm population norm. Why doing it here?
If I am missing the point completely, please correct me, and consider explaining it in simpler words. I could not follow how many such t-tests were run and what was actually compared to what.


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: ONTOGENY OF A SEXUALLY SELECTED STRUCTURE IN AN EXTANT ARCHOSAUR GAVIALIS GANGETICUS (PSEUDOSUCHIA: CROCODYLIA) WITH IMPLICATIONS FOR SEXUAL DIMORPHISM IN DINOSAURS
Review round: 1
Reviewer: 1

Output:
Basic reporting: This is an interesting study of growth and sexual dimorphism in Gavialis and I look forward to seeing it in print in due course. It is generally well written, although it is a bit sloppy at the start. The sample size and size range are both quite positive. It is surprising how poorly studied these crocodilians are. What is their conservation status? Are they endangered? Are there estimates of population size? The recognition of sexual dimorphism at all in crocodilians is quite recent. Who was the first to make such a case? It would be useful to summarize briefly, even in tabular form, the taxa that have been studied and the nature of the sexual dimorphism – e.g., size of structural?  Apart from gharials, is there any other example within crocodilians of structure-based sexual dimorphism?
Experimental design: As far as the nuts and bolts of the study are concerned, I was a little surprised that the study approach was a nuts-and-bolts caliper-based approach. The more modern approach is landmark-based geometric morphometrics, which is well-suited to this study in particular, based as it is on analysis of photos. Nonetheless, I would be hard-pressed to state that the outcome of the study would be different if modern methods were used. As a classical bivariate study, I note the highly correlation among variables. Snout -vent length was reported but it was not selected as the standard variable on the grounds that measures of the snout were variable. With a R2 of 0.93, it is not drastically different from other snout variables, including SMW with  R2 of 0.966. Allometric coefficients are readily interpreted with reference to overall skull length, less intuitively so with skull width. I recommend the former.  In either case, I recommend that the male sample and the female sample be compared by means of a PCA and discriminant function analysis. These are fairly powerful and useful tools.
Validity of the findings: I am still a bit dubious about implications for detection of sexual dimorphism in the fossil record. How can it be that “no dinosaur has been determined to exhibit sexual dimorphism under rigorous analysis?” Is the fossil record really that lousy?! Are sample sizes too low? Is preservation too poor? In the case of sexual dimorphism by size alone, that seems an impossible barrier to cross. But in the case of sexual dimorphism by structure, as in Gavialis, it seems that enhanced sample size should not be required. How rare is this?
Additional comments: l. 44: “hereafter simply ‘dinosaurs’” Thank you so much – this brings tears to my eyes!!!
l. 45: “sexual size dimorphism” – I find this awkward grammatically. Would you consider “sexual dimorphism by size” or “size-based sexual dimorphism?” I hate to divide the phrase/concept “sexual dimorphism.
l. 50: tell us the taxa!
l. 56: elephants and humans have fairly modest growth rates
l. 58: you apply the word “rapidly” both to large mammals and small reptiles. This is sloppy and cries out for more precision.
l. 60: you are making an unexplained correlation between growth rate and sexual dimorphism. Surely sexual dimorphism occurs where it occurs and is often rampant in birds. I think you your problem is more practical than theoretical. Birds grow so fast it is hard to track the development of sexual dimorphism. The real advantage of crocodilians is that they grow slowly over a period of years and thus are excellent for any type of ontogenetic study.
l. 63: I hope you tell us more about sexual dimorphism in crocodilians. I could not have told you that they are often sexual dimorphic with exception of gharials.
l. 222: is “foraging” the best word? It often (but not always) connotes herbivory.
l. 235: bullae are NOT a visual signal, are they? “these features” implies that they are.
l. 250: bullae in alligators vastly more modest than those of gharials. I hesitate to call them similar.
l. 310: what about the possibility that an inflated bulla actually increases the surface area for origin of palatal muscles? It is not necessarily a negative.
l. 352: thank
l.376:  andevolutionary
Fig. 2 the nasopharyngeal duct is a soft-tissue structure contained within the palatines. The figure incorrectly labels the palatines as the duct itself.
Fig. 5. The slope of the RMA plots is the allometric coefficient itself? So state and include slope on plot itself.
I recommend that tables S1 and S2  be included with the text rather than being in the supplemental files.


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: ONTOGENY OF A SEXUALLY SELECTED STRUCTURE IN AN EXTANT ARCHOSAUR GAVIALIS GANGETICUS (PSEUDOSUCHIA: CROCODYLIA) WITH IMPLICATIONS FOR SEXUAL DIMORPHISM IN DINOSAURS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Throughout the text the authors mainly have a consistent formatting style. I find it a little difficult to read in places because of multiple run-on sentences that contain too many thoughts and clauses. There are some issues with spelling and punctuation, and I corrected some of these. Please check the manuscript carefully.

The focus of this manuscript is extant taxa but aimed to collect predictive data for extinct, and as such the authors used morphological features that could be preserved in the fossil record. However, I found that the discussion focused more on what the structures could be for (rather than if there was a clear male/female distinction useful for fossils) and began to veer away from the main theme and (briefly) address ecological and dietary implications for the extant. Though these are important points to consider, I found that I wanted there to be more discussion and supporting data or references for several of the statements made (e.g. the resonance capabilities of the pterygopalatine bullae, the ability to deal with larger prey). Some things need to be addressed earlier in the text (the definition of what the bullae actually are), and that would make the paper flow a bit better.

Figures are extremely important for anatomical descriptions. In general, I found the figures here to be fairly informative. A comparative image of the pterygoid bullae of Gavialis and Alligator (because it was mentioned in the text) would be useful, as would comparative images of the largest and smallest individuals to see similarities and differences in the ghara/fossae across the size range sampled. The caption for Figure 1 is missing reference to image F- a small oversight. In general, the authors could have a few more call outs to the figures in the text.
Experimental design: The authors add to our knowledge of the ghara in Gavialis. However, I still wish that there was more concrete data for male/female of the specimens in order to avoid any circularity around size. The 2D measurement data are important variables for looking at shape change as related to size, and I think these could be complemented with some qualitative statements regarding the morphological differences among the ghara observed. I’m not certain that the authors actually tested sexual selection here, even though that is a prominent aspect of the title.
Validity of the findings: The authors discuss their results in terms of statistics, and I do not have the necessary background to comment on the appropriateness of the methods used. Their findings support what we already say: that the largest individuals are males, have ghara, and have enlarged bullae. The asynchronous appearance of skeletal maturity, ghara appearance, and bulla inflation appear to be new findings, or at least are more clearly documented here. I’m not sure that the appearance of these morphological features is as clearly tied to sexual selection (as in the authors’ title) as it could be (was this actually tested here?), and the ‘implications for sexual selection in dinosaurs’ (also in title) could be more clearly stated (right now, I’m interpreting the implications as ‘we still don’t have enough data to know in dinosaurs’- correct?).
Additional comments: This paper presents a new compilation of data on an interesting morphological structure. This paper needs some slight cleaning up throughout and more focus in the discussion. The quantification of these features through size (=ontogeny here) represents a step toward trying to interpret sexual dimorphism in the fossil record, a notoriously tricky thing. If the presence or exaggeration of these features may have ecological or trophic implications (which is reasonable), the authors need to add a bit more to frame those statements more clearly.


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: ONTOGENY OF A SEXUALLY SELECTED STRUCTURE IN AN EXTANT ARCHOSAUR GAVIALIS GANGETICUS (PSEUDOSUCHIA: CROCODYLIA) WITH IMPLICATIONS FOR SEXUAL DIMORPHISM IN DINOSAURS
Review round: 1
Reviewer: 3

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


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: ONTOGENY OF A SEXUALLY SELECTED STRUCTURE IN AN EXTANT ARCHOSAUR GAVIALIS GANGETICUS (PSEUDOSUCHIA: CROCODYLIA) WITH IMPLICATIONS FOR SEXUAL DIMORPHISM IN DINOSAURS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have made changes to make the text more readable, though I still maintain that the sentences are quite long. It is better though. The rearrangement of several sentences/short sections was helpful as well. I've fixed a few more grammatical and spelling issues that I found.

Figures are improved- thank you for including the comparative image of the alligator pterygoid bullae.
Experimental design: Though I am still concerned about circularity of data by assigning 'male' to the largest specimens without that actually recorded, the authors did add some text to qualify that this is an assumption. This could be made even more explicit by saying 'presumed male' rather than 'male' in all cases.

I also still agree with other reviews concerned with whether sexual selection was actually tested rather than just presence of sexual dimorphism. True, this is laid out as a hypothesis that can be tested with additional data in the future, but I'm still skeptical about it here.
Validity of the findings: The size of the dataset is emphasized repeatedly- yes, it is quite large and the authors are commended for accumulating those data. I still maintain that the findings are not entirely surprising. In the authors' response regarding dinosaurs in which a large enough sample exists to test sexual dimorphism, they bring up Coelophysis. However, this taxon was shown to exhibit a broad range of intraspecific variation in developmental patterns (Griffin 2018) rather than a bimodal dimorphic set of morphological features.
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 RELATIONSHIP BETWEEN ADOLESCENT OBESITY AND PELVIS DIMENSIONS IN ADULTHOOD: A RETROSPECTIVE LONGITUDINAL STUDY
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article is mostly written in clear English throughout, and the literature review is thorough. The structure conforms to PeerJ standards. Figures are relevant, but some could be improved for clarity. The raw data Is supplied.

See below for specific comments:

Line 22 - Is "pathogenic" a necessary descriptor here?
Line 25 - add descriptor for "final height" - reduced? - spell out DM2, and "afterward lost their weight" is an awkward phrasing in English - subsequently lost weight?
Line 27 - delete "however, does" replace with "is"
Line 28 - delete "fully apply in", change "case of" to "case in" or "case for"; add "skeletal" before "differences"
Line 38 - add "(BIA)" after analysis
Line 49 - qualify what you mean by "satisfactory sensitivity..."
Line 53 - add "and gait pattern" after "activity"
Line 57 - Do you really want to start the paper with a definition from WHO? I suggest laying out the problem or question briefly with a strong impact in the beginning of your introduction
Lines 64-65 - I would delete the sentence "In comparison to individuals...getting married" as this is not extremely relevant and you don't mention it further.
Line 66 - add "of comorbidities" after "overview"
Line 70 - awkward wording for "individual's overweight..." maybe just delete "overweight", because it is the adjective and "obesity" is the noun
Line 73 – delete “another” replace with “a”
Line 75 – this is not exclusively a holistic perspective from toxicology – maybe generalize this to “perspective of a pathologist” – and it is problematic to think of fat and fat storage as purely pathological.
Line 84 - see comment for line 25
Line 108 – specify development in juveniles
Line 110 – should be “epiphyseal”
Line 118 and 119 – define ICIC a little better and refer to it also as the osteometric measurement of “bi-iliac breadth”
Line 124 – delete “on the” and replace with “in”
Line 125 – add “s” to be “animal models”
Line 145 – change “Caucasian Population” to “European ancestry”
Line 150 – specify number of females and males, instead of percentage of females – this is misleading
Line 152 – type – Tanita – second time – and include hyphen between SC-240
Line 153 and 154 – Should this be Salimetrics, LLC. This is what their website says.
Line 161 – Why are you not also using BIA for level of obesity/adiposity here?
Line 174 – Specify data is “nonparametric” if using Mann-Whitney and Spearman’s rank
Line 185 – Again, why not using BIA?
Line 198 – “The relationship was stronger for recent adiposity”? this seems like the reverse of what you found. Please explain this variable.
Lines 203-205 – Is there bias when conducting anthropometrics with higher versus lower adiposity? How can you ensure that soft tissues do not have an effect on the measure in terms of tissue depth?
Line 209 and 211 – spell out AUC
Line 216 – explain this finding more
Line 221-222 – “illustratively exhibited” is a little redundant – maybe “clearly illustrated”
Line 227 – “retrospective anthropology”? just say “anthropology”
Line 236 – add “approach” before “falls”
Line 238 – Delete “of an image”
Line 248 – Normal population – are you comparing to both males and females? If not then perhaps just “average weight females”
Lines 248 – 251– the sentence starting “In consistency with this, we assume…” Assume? Didn’t you just demonstrate/test this hypothesis?
Lines 253 – 255 – is this also associated with the same rate of increase in obesity rates?
Line 256 – “alarming” – this is dramatic – Other research may find extremely deleterious effects of obesity, but higher estradiol and wider pelvis are hardly life threatening.

Table 1 – the first 2 rows are not listing the age during enrollment and follow up. Additional columns would resolve this issue, as opposed to having these as extra rows.

Somewhere in the discussion, it should be addressed that gait changes associated with obesity can lead to changes in bone shape. Obese subjects walk with a more side-to-side saunter which appears to cause forces to change the shape of the bones of the femur and presumably the pelvis. Here are some references that deal with these changes in bone shape.

Agostini GM, Ross AH (2011) The effect of weight on the femur: a cross-sectional analysis. J Forensic Sci 56:339–343

Elliott M, Kurki H., Weston, DA, Collard, M., (2015) Estimating body mass from postcranial variables: an evaluation of current equations using a large known-mass sample of modern humans, Archaeol Anthropol Sci, DOI 10.1007/s12520-015-0251-6

Hills, AP, EM Hennig, NM Byrne and JR Steele. 2002. The biomechanics of adiposity-structural and functional limitations of obesity and implications for movement. Obes Rev 3:35-43.

Lacoste Jeanson A, Santos F, Villa C, Dupej J, Lynnerup N, Brůžek J, (2017) Body mass estimation from the skeleton: An evaluation of 11 methods. Forensic Sci Int. Dec;281:183.e1-183.e8. doi: 10.1016/j.forsciint.2017.10.026.

Moore MK, Schaefer E (2011) A comprehensive regression tree to estimate body weight from the skeleton. J Forensic Sci 56: 1115–1122

Moore MK. 2008. Body mass estimation from the human skeleton. PhD Dissertation. University of Tennessee, Knoxville.

Moro M, Van der Meulin MCH, Kiratli BJ, Marcus R, Bachrach LK and Carter DR. 1996. Body mass is the primary determinant of midfemoral bone acquisition during adolescent growth. Bone 19(5):519-526.
Experimental design: The research falls within the aims and scope of journal, the research question is well defined, the research is rigorous and methods apt.
Validity of the findings: The conclusions appear sound. There could be other confounding variables in terms of gait changes which are mentioned at the end of the "basic reporting" section.
Additional comments: No additional comments


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

Input:
Title: THE RELATIONSHIP BETWEEN ADOLESCENT OBESITY AND PELVIS DIMENSIONS IN ADULTHOOD: A RETROSPECTIVE LONGITUDINAL STUDY
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper needs to be edited. As presented there are areas that are unclear and ambiguous.
The literature references is minimally sufficient.
The hypotheses are stated but the data is over interpreted.
The research appears to be original and within the aims and scope of the journal
Experimental design: The methods do not have sufficient detail to replicate
Validity of the findings: See general comments below. I believe the data may be over interpreted and there is a lack of discussion of other possible causal factors
Additional comments: This is an interesting and important study that examines the relationship between adult pelvic breadth relative to stature and adiposity. It is a retrospective study, so the research design does not allow the researchers to determine the causation of the correlations. While a limiting factor, especially the lack of hormonal data for females, it does not take away from the study. There are, however, some problems with the presentation of the research that needs to be addressed, especially since there are limitations associated with the retrospective study. For the methods there is very little information about how they controlled for body fat in the measurements, how stature was measured, how sensitivity and specificity were calculated, the BMI of the individuals during the original and follow up study. This information is necessary for the reader to understand the interpretation of the results. Regarding the interpretation, the main problem with this study is that there are a lot of assumptions and a lack of discussion of other possible causal factors. For example, there needs to be some discussion of normal pelvic width increases with age in adulthood and the difference in growth between males and females. For example, when does pelvic breadth complete growth in males and females and is the interpretation affected by the age difference between the males and female in their sample?  Furthermore, stature is reduced in obese adolescents, at least among females, indicating that obese females should have a higher pelvic breadth/stature ratio even if the pelvis is not widening. In the graphs there is no indication of which individuals were of normal BMI or obese. For the males in your sample, there is little correlation with testosterone and relative pelvic breadth if males with extreme testosterone are removed. Again, were the individuals with high testosterone of normal BMI or where they obese? In addition , I am not sure you can make the broad argument that this study shows the limits of forensic anthropological methods without giving specific details. I assume the authors are referring to the use of pelvic breadth and stature to estimate body mass. However, the papers they cite are not forensic anthropological but rather paleontological where the goal is to reconstruct lean body mass when there were unlikely very few obese individuals.
Line 103 – what does this topic sentence have to do with the rest of the paragraph? There should be a separate paragraph that discusses the effects of low testosterone. Much of the paper needs to be edited for clarity and flow.
Table 1 – information on BMI of sample. It might also be interesting to know how many of the initial participants that were obese remained obese as adults
Figures 4-6  – no red dot


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 RELATIONSHIP BETWEEN ADOLESCENT OBESITY AND PELVIS DIMENSIONS IN ADULTHOOD: A RETROSPECTIVE LONGITUDINAL STUDY
Review round: 1
Reviewer: 3

Output:
Basic reporting: Generally, I found this paper was well-written and the author's main points were clear and unambiguous.

The table requires substantial revision (details in notes to authors)
Experimental design: The question is well-defined and relevant and makes a contribution linking hormones and skeletal morphology, although this manuscript would benefit from further background regarding endocrinology, inflammation, and obesity.
Validity of the findings: Conclusions are generally valid, but some of the theoretical linkages may be tenuous. Further details are below in comments to the authors.
Additional comments: In this paper, the authors examine the relationship between obesity during adolescence and pelvic breadth, based on the relationship between adipose tissue and estrogenic activity. They found that adiposity (measured with bioimpedance) was related to pelvic breadth in adulthood, and pelvic breadth in adulthood was a retrospective marker of obesity during adolescence. They did not find a significant association between salivary reproductive hormones and pelvic breadth.

Overall, I think it would be an interesting addition to the literature about how conditions during growth and development shape adult health and skeletal phenotype, but it requires a few clarifications and a bit more analyses.

In general:
The authors switch between using the terms “obesity” and “adiposity”, and at times this is confusing, as adiposity seems to be the theoretical driver of hormonal changes that affect the pelvis. In comparison, the author’s definition of obesity is unclear (what is the threshold for obesity?) and I’m not sure if in the current form it adds to the main narrative and argument presented here.
I would recommend either further developing the model presented in the introduction (more detail in background and discussion) or removing it.

Specific recommendations:
1.	Abstract
a.	The abstract describes collecting salivary samples for measurement of testosterone and estrogen, but estrogen was not reported in results?
b.	“Anamnesis” is an unusual term to use here. I assume the authors use it to refer to medical history, but they then don’t report any kind of medical history?
c.	Estrogen is mentioned in the typeset Abstract Background, but not in the draft (lines 39-40), and it is not included in the rest of the manuscript.

2.	Introduction
a.	I would recommend the authors also include some references on how social stigma (such as incurred by obese people in a fat-shaming world) can affect inflammatory and stress pathways. Some of the physical and psychological effects of obesity are likely linked to these social experiences of bullying and exclusion.
b.	The model proposed in lines 73-78 about analogizing obesity as a toxic substance is not really developed further or revisited in the rest of the manuscript, so I’m not sure why it is included here.
c.	In line 100-101, the authors mention fat tissue being correlated with the level of estrogens, but then both references focus on estrogens in men. Perhaps include some references about healthy adult women, such as Ziomkiewicz et al (2008), or focus this manuscript on males?
d.	Given that this isn’t a specialty journal, a diagram of the ICIC measurement might be useful for some readers.

3.	Materials and Methods
a.	Line 145: The Czech sample is likely better described as “white” or “Central European” instead of “Caucasian”, although it is not clear if the sample was screened for racial or ethnic identity?
b.	Line 149: I’m unsure what probands you are referring to?
c.	Lines 156-158: It would be helpful to provide additional detail regarding collection of salivary testosterone. How long after eating/drinking/brushing teeth? Was gum used to stimulate salivary production? Was the saliva collected before, during, or after the rest of the examination?
d.	Lines 161-163: Please provide the thresholds for BMI standard deviation scores so we know the cutoffs you used for classifying “obesity” in this sample.
e.	Table 1 needs to be reformatted so the row and column labels are accurate.
4.	Results
a.	Descriptive statistics correlating adolescent body fat and adolescent BMI would be useful, as from the reported information it’s clear you could test whether adiposity and BMI are related vs whether increased BMI is associated with increased musculature.
b.	As part of the descriptive statistics, I would be interested to know whether people who were obese or had high adiposity as teenagers maintained that status into adulthood
c.	Lines 202-211: Without a clear definition of the BMI threshold for obesity, or any understanding about whether high BMI was associated with high adiposity, I’m unclear about whether the ICICH ROC analyses are useful. I wonder what would happen if the analyses were performed in reverse…correlating adolescent BMI and ICICH, then constructing a ROC curve for ICICH and adiposity?
d.	Lines 204-206: Please provide sample size for the number of individuals with and without a history of obesity. This could be provided as part of a revised table 1, or in text.
e.	Lines 213-216: your subtitle says “ICICH as a marker of estrogenization”, but estrogen isn’t measured? Based on Figure 7, I’m not sure if a linear regression is the best method for examining the relationship between testosterone and ICICH.
5.	Discussion
a.	Further development of the author’s arguments regarding estrogen and testosterone in adolescents and men is needed, bolstered by references from endocrinology. I’m unclear that increased estrogens are necessarily associated with reduced testosterone, and it’s been shown that testosterone is converted to estrogen in bone tissue. This means there are several theoretical and biological linkages that could be strengthened in the argument between BMI --> adipose tissue --> estrogen --> testosterone/bone morphology.
b.	Line 256: I’m unsure why the authors find the observation of increased pelvis breadth “alarming” based on this discussion.
c.	Finally, please spend a bit more time discussing the potential differences between high BMI (which can be caused by body fat or muscle mass) and high adiposity.

Ziomkiewicz, A., P. T. Ellison, S. F. Lipson, I. Thune, and G. Jasienska. “Body Fat, Energy Balance and Estradiol Levels: A Study Based on Hormonal Profiles from Complete Menstrual Cycles.” Human Reproduction 23, no. 11 (2008): 2555–63.


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 RELATIONSHIP BETWEEN ADOLESCENT OBESITY AND PELVIS DIMENSIONS IN ADULTHOOD: A RETROSPECTIVE LONGITUDINAL STUDY
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Greatly improved and interesting study.
Line 60 - delete "yet"
Lines 71-77 - is this really necessary? it is not discussed again nor does it seem to influence your results.
Line 127 - Sentence "However, in the case of the juvenile pelvis, it does to fully apply" is a little confusing. Try just adding it to the previous sentence so it reads something like "...adult pelvis is sexually dimorphic while the juvenile pelvis is not."
Line 129 - morphological differences BETWEEN SEXES are distinct.
Line 151 - You state the next stage is to validate if relative pelvic breadth can be used as a classifier of the history of obesity. It is still unclear as to why you want to predict if someone was obese as a juvenile. The research question is does obesity during adolescence influence the pelvic breadth to stature ratio? But why predict obesity as a juvenile? Couldn't you just ask the patient? This could be corrected with a single sentence.
Line 189 - replace "bi-iliac" with "bi-spinal." You state in 186 that bi-iliac breadth can be influenced by soft tissue and then on 189 say that the advantage of bi-iliac breadth is that there is not interaction with soft tissues.
Line 245 - You never define ICICH in the text. You could go back to line 190 and add them so it looks something like Both pelvic dimensions were analyzed in relation to body height and indicated as ICICH and ASISH.


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 RELATIONSHIP BETWEEN ADOLESCENT OBESITY AND PELVIS DIMENSIONS IN ADULTHOOD: A RETROSPECTIVE LONGITUDINAL STUDY
Review round: 2
Reviewer: 2

Output:
Basic reporting: No additional comments
Experimental design: No additional comments
Validity of the findings: No additional comments
Additional comments: The authors have mostly addressed my concerns and I feel the manuscript is generally acceptable.

In Figure 7 the asterisks (*) are not explained in the figure legend or text. Additionally it might be more effective as a boxplot instead of a bar chart, since I believe it represents an estimate and range, rather than count data.


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

Input:
Title: THE SPINDLE ASSEMBLY CHECKPOINT AND SPECIATION
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript explores the idea that chromosomal rearrangements during mitosis may be a primary driver of speciation. This is not a new hypothesis and previous criticisms were mostly based on the reproductive incompatibility with the ancestral karyotype. The authors in this study however claim that considering partial fertility of heterozygous may allow the separation of a new species as they show using mathematical modeling. They also introduce the concept of dynamics of the SAC (whose molecular regulation has been deeply studied in the last decade) as a factor contributing to speciation. Overall, this is an interesting topic that is well introduced and discussed in the manuscript.
Experimental design: Overall, I don’t have specific comments on the mathematical modeling as it is beyond my expertise. My comments mostly related to some definitions used in the introduction and related conclusions.
Validity of the findings: SAC. Lines 75-95. The authors basically present the SAC as a mechanism that senses lack of tension, in part through the activity of aurora kinases. This is not strictly wrong. However, experts in SAC do not have a complete agreement on whether the SAC senses tension or attachment. I would say that most authors prefer the attachment as the major molecular event monitored by the SAC. Accordingly, kinases that monitor attachment such as MPS1 are core components of the SAC. Many authors do not consider aurora kinases as core components of the SAC, but complementary activities that induce de-attachment upon reduced tension. This discussion does not change the main message of the manuscript, but it may be convenient to introduce the discussion between attachment and tension.

Even if the previous discussion is properly discussed in the manuscript, I still have problems understanding the relevance of the SAC in speciation (especially given the relevance given to SAC in the title, abstract, introduction and part of the discussion). In fact, they claim that their study is novel when compared to classic papers because they have introduced SAC dynamic concepts in their work. However, I think the authors could have written the same manuscript and obtaining the same conclusions without referring to the SAC at all. The main assumption for their conclusions is the partial fertility of the heterozygous, but this is equally possible whatever SAC properties are. I cannot evaluate the mathematical expressions in their algorithm but I really wonder whether any specific SAC property has been used there.

In addition, many SAC properties are really different in different species. For instance, SAC ablation in mitotic cells does not induce any deficiency in flies but it is lethal in mammals. Again, I have the impression that this is not really relevant for the manuscript because SAC properties are not really part of the algorithm used.

Some sentences are difficult to understand or are perhaps not properly sustained by the data or concepts used in the manuscript. For instance (line 422) “the dynamics of the SAC provide the main mechanism of those rearrangements”.. I would say that these rearrangements happen even despite the SAC, or because the SAC is not efficient enough, but saying that the SAC provides the mechanism for these re-arrangements seems counterintuitive. Perhaps the authors imply that the fact that the SAC is not efficient enough has been selected to allow evolution? But the way these concepts are used is not clear for this reviewer.

Finally, the SAC has been deeply analyzed in mitosis (and by extension very likely may apply to meiosis II), but how the SAC works in meiosis I (the expected scenario for most of the discussion in the manuscript) is not really understood and perhaps the authors may extend more in detail these implications.

The idea that a parallel mutation occurred together with the arrangements is attractive, but I wondered whether the authors have evaluated that the re-arrangements per se are “the” mutation. For instance, re-arrangements can kill genes or place now enhancers in the vicinity of some genes. In some cases, it has been proposed that reduced number of chromosomes may facilitate prometaphase, so perhaps just reducing or increasing the number of chromosomes per se may have some advantages or disadvantages.
Additional comments: N/A