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: INTERSPECIFIC VARIATION IN THE LIMB LONG BONES AMONG MODERN RHINOCEROSES—EXTENT AND DRIVERS
Review round: 2
Reviewer: 1

Output:
Basic reporting: In the revised manuscript titled “Interspecific variation in the limb long bones among modern rhinoceroses - extent and drivers”, Mallet and co-authors present a thorough revision of their initial article investigating upper limb in modern rhinoceroses using a three-dimensional geometric morphometric approach. I am happy to see the inclusion of a clear testable hypothesis, which is shown to be partially supported by their Results and built upon in the Discussion and Conclusion. The revised article is well written and the points are put across in a logical manner, with notable improvement to the grammar. Unfortunately, I do not wholly agree with the authors that they have fixed all the problems with regards to wording. I am uncertain whether the authors revisited some of the sentence structure mentioned in my initial review, as there are still several instances where swapping the adjectives and nouns make the sentences make more sense and flow more smoothly – this is especially evident (to me) while reading the Results section. I have offered some suggestions for sentences which I feel are still a bit clunky, or that I feel would benefit from rearrangement (see Comments to Authors); however, I stopped suggestions after the Humerus and Radius sub-sections to prevent an overly laborious list of “suggest change to” comments. I recommend that the authors go over the descriptive sentences in the results and ensure that the adjectives and nouns are in a logical order. I stress that this is not the case for every descriptive feature, and the authors have in general done a very good job of fixing the previous grammatical errors. Many of these adjective-noun suggestions are very minor, and some may simply be personal preference – I defer to the authors’ viewpoints on whether these warrant changing or not.
Beyond the additional grammatical suggestions, I find the tables, figures, references and supplementary information remain well laid out, logical, easy to understand, and any previous comments I made have been addressed. The few key references I felt would assist the article have been incorporated in a concise and appropriate manner, and have improved the background for the study.
Experimental design: At risk of regurgitating my previous review, I feel this article is well suited to the aims and scope of PeerJ as it represents an original research article within the biological sciences, performed to a high technical standard. The authors lay out several issues and knowledge gaps (e.g. the label of "graviportal" and whether rhinoceroses can be considered as such). The authors lay out their reasons for chosing rhinoceroses as a subject group well, with logical arguments. They then accumulated an excellent sample of modern rhinoceros upper limb bones, and have used more computationally intensive methods than were previously available to researchers studying locomotor morphology in these animals. The methodologies used are well laid out and informative, and any missing information from the original article has been provided. The results remain comprehensive in their anatomical detail, and following the rebuttal I now have a beter understanding about why the descriptions are written as they are. The discussion is good, with sound descriptions and comparisons, and I am happy to see the authors delved further into the mechanical implications of the shape variation they observed, including comments on myology alongside osteology. My main criticism of the original article (lack of specific research question and testable hypothesis) has been rectified, and the results and discussion are the better for it.
Validity of the findings: Essentially in repetition of my previous appraisal, the findings of this study most definitely benefit the wider literature. The results for interspecific differences between the different rhinoceros species will be valuable for any future studies based on rhinoceros locomotion, graviportality, or general perissodactyl biology. All data utilised for the study have been provided for the reviewers in well organised supplements or ancillary table and figure files, and from what I can tell the methodologies are robust, statistically sound and controlled. Concerns I voiced about the high dimensionality of the data remain, but I am satisfied with the comments from the authors in the rebuttal such that I no longer think this is an issue for the article itself – more a philosophical issue for dimension reduction in landmark analyses. With the inclusion of a discrete hypothesis, I feel the conclusions are apt and concise. Speculation throughout the Discussion was limited, although comments from the authors in the rebuttal clarified reasoning, for which I am grateful. Overall I believe this is a much improved manuscript, and the findings therein will be of great value in potential future works on graviportality, large mammal locomotion and perissodactyls in general.
Additional comments: I am very pleased to see the authors chose to revise this manuscript – I maintain that it is a very good article with solid arguments for the choice of taxa and methodology, and a well-rounded discussion relating to the results that were obtained. I find this revision a much-improved version of this article. I have some minor comments on content, however the majority of the below comments are suggestions for rearrangement of sentences to enable easier reading, rather than issues with the statements being made.

Introduction – very minor comments and requests
Line 79-80: “However, the peculiar morphology of hippos (barrel-like body and shortened limbs) linked to semi-aquatic habits” – I have seen this mentioned before, but could you include a citation which describes this link?

Line 82-83: “Rhino’s graviportal condition is surely the less agreed upon:” – I feel like this sentence still needs some rearrangement – perhaps something like: The graviportal condition in rhinoceroses is surely the least consensual:

Line 98: “[Indian Rhinoceros]…survive in India…” – Very minor comment, but I believe this species is also extant in Nepal (see IUCN Red List 2008), although I am uncertain whether Dinerstein (2011) also included this population.

Line 135-137: “This effect is supposed to be more pronounced on the stylopodium (humerus and femur) than on the zeugopodium (radius, ulna, tibia and fibula) bones” – I know exactly what you mean, but due to the fickleness of the English language this may be read as the effect “should” be more pronounced (i.e. “is supposed to be”), which is more a statement than a hypothesis. I recommend a very minor alteration for clarity: We predict that this effect will be more pronounced…

Line 139-140: “In addition, we expect a potential effect of the phylogenetic heritage and of the different ecologies of the species.” – The hypothesis is sound, but I think there is too much vagueness in ‘expect a potential effect’, so perhaps just: In addition, we expect an effect of phylogenetic heritage and different species’ ecologies on bone shape.

Material and Methods – no requests, just questions/comments
Line 245-246: “we used a Principal Component Analysis (PCA) to reduce dimensionality” – did the authors use a between-group PCA approach, or a classic one? A very recent preprint study has suggested that bgPCA can hit problems when dealing with high variable numbers (e.g. multiple semi-landmarks), so I thought I would check whether a bgPCA was performed here. If not, please ignore this comment. If it was, perhaps the authors can comment on the rationale behind it, bearing in mind the potential problems. Reference: Cardini, O’Higgins, Rohlf (2019) Seeing distinct groups where there are none: spurious patterns from between-group PCA, bioRxiv pre-print.

Line 253-255: “Neighbour Joining method was used to construct trees based on relative Euclidian distances between individuals based on all principal component scores obtained with the PCA” – I understand the explanation given in the rebuttal, and have no further comment on the article. I do feel however that the greatest benefit of the N-J tree method is to investigate the spread or variation in raw shape coordinates, which as the authors point out is not possible with landmark-heavy datasets. A philosophical point, nothing more!

Results – minor comments, mostly sentence rearrangements
Line 300-301: “a shaft with its maximal width situated between the head neck and the deltoid tuberosity” – I think the authors mean “humeral head” here instead of “head neck”

Line 302: “a distal epiphysis very large because of…” – suggest change to “a very large distal diaphysis due to…”

Line 303-304: “a medial epicondyle mediolaterally wide and craniocaudally compressed” – suggest change to “a mediolaterally wide and craniocaudally compressed medial epicondyle”

Line 304-305: “…compressed olecranon fossa and trochlea, a wide trochlea displaying…” – suggest change to “…compressed olecranon fossa and trochlea; a wide trochlea displaying…”

Line 308: “overhanging caudally the diaphysis.” – suggest change to “overhanging the diaphysis caudally”

Line 310-311: “a slightly marked lesser tubercle convexity whereas the greater tubercle one is massive” – what does “slightly marked” mean in this context? If you mean the convexity is marked (as in markedly obvious), then it stands to reason this cannot be “slight”. Please clarify.

Line 314-315: “a medial epicondyle craniocaudally developed and overhanging the olecranon fossa;” – suggest change to “a craniocaudally developed medial epicondyle overhanging the olecranon fossa”

Line 315-316: “with an axis less dorsoventrally tilted” – suggest change to “with a less dorsoventrally tilted axis”

Line 323: “a distal epiphysis proximodistally extended” – suggest change to “a proximodistally extended distal epiphysis”

Line 326-327: “a distal epiphysis mediolaterally stretched…” – suggest change to “a mediolaterally stretched distal epiphysis…”

Line 342-343: “a protruding lateral insertion relief (i.e. insertion area of the m. extensor digitorum) whereas the radial tuberosity is little prominent” – I have two small comments here; 1) I have found an English text (Budras et al. 2012, Anatomy of the Horse) in which this feature is named the “lateral coronoid process”. 2) there is no muscle (to my knowledge) in the perissodactyl forelimb termed simply the “m. extensor digitorum” – there is the common digital extensor (m. extensor digitorum communis), which originates from the lateral epicondyle and epicondylar ridge of the humerus; and the lateral digital extensor (m. extensor digitorum lateralis), which originates from the lateral epicondyle and (potentially) has some fibres originating at the lateral coronoid process. From my observations however, this process/relief is primarily the site for the insertion of the lateral-collateral ligaments binding the elbow together. I do not think that the term needs changing, but the definition provided by the authors does need revision.

Line 343-344: “a lateral synovial articulation surface for the ulna mediolaterally reduced” – suggest change to “a mediolaterally reduced lateral synovial articulation surface for the ulna”

Line 350-351: “an articular surface for the scaphoid little extended proximally” – suggest change to “a slight proximal extension to the articular surface for the scaphoid”

Line 353-354: “a proximal articular surface less asymmetrical despite the development of the medial part” – suggest change to “a less asymmetrical proximal articular surface, despite the development of the medial part”

Line 355: “a completely flat radial tuberosity” – did you observe any differences in relative size of the radial tuberosity relative to (for example) the radial head? If so, did this relative size difference correlate with size/phylogeny? Just a functional thought…

Line 355-356: “a lateral synovial articulation for the ulna mediolaterally stretched” – suggest change to “a mediolaterally stretched lateral synovial articulation for the ulna”

Line 359-360: “a distal epiphysis far less dorsoventrally compressed and a lateral tubercle on the dorsal side poorly developed” – suggest change to “a less dorsoventrally compressed distal epiphysis and a poorly developed lateral tubercle (on the dorsal side)”

Line 360-362: “a distal articular surface dorsoventrally wide with the surface responding to the scaphoid extending proximally” – suggest change to “a dorsoventrally wide distal articular surface, with the surface corresponding to the proximal extension of the scaphoid”

Line 366-367: “R. unicornis’s extension along the second axis is very limited, contrary to that of C. simum and D. sumatrensis clusters.” – suggest change to “Extension of R. unicornis morphospace occupation along the second axis is very limited, contrary to that of C. simum and D. sumatrensis clusters.”

Line 370-371: “a palmar process opposed to the coronoid process proximally reduced” – suggest change to “a proximally reduced palmar process, opposed to the coronoid process”

Line 371-372: “a distal epiphysis dorsoventrally broad, with a developed lateral prominence” – suggest change to “a dorsoventrally broad distal epiphysis, with a relatively developed lateral prominence”

Line 372-373: “a little developed radial styloid process; an articular surface for the scaphoid proximally extended.”
- Here I will stop making suggested changes for sentences –

Line 383-384: “a massive olecranon tuberosity with a medial tubercle – where inserts the medial head of the m. triceps brachii – oriented dorsally” – an enlarged medial olecranon tubercle also offers greater attachment and mechanical advantage for the ulnar insertion of the superficial and deep digital flexors (involved in maintaining forelimb posture, especially in very large animals). See also Line 393-394.

Line 388: “a broad shaft with a triangular section” – insert “a broad shaft with a triangular cross-section”

Line 390: “(i.e. triquetral or pyramidal bone)” – the palaeontological name for this (certainly in the USA) is the cuneiform

Line 418-419: “D. bicornis and R. unicornis specimens overlap a significant part of the cluster of C. simum” – very nit-picky comment, but may be worth avoiding “significant” in this context in favour of “substantial”, just in case a reader assumes that there was a test for significant difference between morphospace occupations.

Line 424: “concave aspect to the diaphysis axis” – suggest removing “axis”.

Line 553-554: “forming two distal tips responding to the two lateral tubercles” – two distal tips corresponding (?) to…

Line 656-657: “associated to” – there are several instances of this phrase, where I believe the authors mean “associated with”

Line 675: “Linear regressions of shape scores against log-transformed centroid size (Fig. 9)” – here I think you mean multivariate regressions

Discussion – minor content comments
Line 741: “resembles the tapirs’ one,” – suggest “resembles that of tapirs,”

Line 747-750: “Watson & Wilson (2007) showed that the m. supraspinatus in horses acts more as a shoulder stabilizer than as a true extensor of the shoulder. Given the qualitative similarity of shape of this joint between African rhinos and equids, it is likely that this muscle plays a similar role among these groups.” – Would the authors therefore also speculate that the supraspinatus of Asiatic rhinoceroses (with large greater tubercles forming a deep bicipital groove acts in a similar manner to that of tapirs or suids (which also exhibit a very large greater tubercle; Barone 2000), and likely maintains an essential extension component rather than primarily a support role (as in hippopotamids; Fisher et al. 2007)?

Line 750-751: “The robustness of the lesser trochanter is consistent with a development of the medial part of the m. supraspinatus, to increase the shoulder stabilisation.” – what do the authors mean by “a development of the medial part of the m. supraspinatus”? Do they refer to the supraspinatus insertion site? The medial supraspinatus is, technically, attached to the scapula. Please clarify.

Line 755-761: “The development of a massive greater tubercle is encountered among hippos (Fisher, Scott & Naples, 2007) and may be interpreted as a direct link with semi-aquatic habits and displacements into muddy swamps or riverbanks. This particular morphology is yet also encountered among domestic bovids for example (Barone, 2010a), which are not semi-aquatic. Conversely, extinct Amynodontidae, presumed to have been semi-aquatic Oligocene rhinos (Averianov et al., 2017), did not display this greater tubercle development (Scott & Jepsen, 1941).” – The authors mention in their rebuttal that “in the current state of knowledge, it seems difficult to hypothesise a valuable reason for this convergence”, and yet they then make a direct link between this feature and semi-aquatic lifestyle. I feel that their secondary theory of the enlarged greater tubercle as a potential indicator of shoulder extension/support in resistance to displacement on compliant substrates (useful for suids, hippopotamids, tapirs, dicerorhinines etc.) is a more logical step. Perhaps soften the semi-aquatic angle in favour of the compliant substrate theory, and maybe add a remark on what future work could be focussed upon in order to clear up this curious convergence (as provided in the rebuttal).

Line 800-801: “this trait seems more likely related to phylogeny, African species having a more horizontal plateau than African ones.” – there is something amiss here. I suggest including a semi-colon (;) after “phylogeny”, and then one of the “African” should probably change to “Asiatic”

Line 840: “a larger insertion area for the medial head of the m. supraspinatus” – there is no medial head of the supraspinatus as such, as it is a single-belly muscle. Perhaps modify this to “a larger medial insertion area for the m. supraspinatus”

Line 843-844: “This configuration has been previously interpreted as a mechanical advantage for muscles inserting on the shoulder” – this sentence is not quite right; either the configuration “confers increased mechanical advantage for the muscles”, or it is “mechanically advantageous for the muscles” – neither of these are wrong, but the current text does not really make sense.

Line 846-847: “The development of the lesser trochanter may also help supporting the scapula…” – I think the authors mean the lesser tubercle, not trochanter.

Line 872: “possibly allowing a mediolateral weight display” – weight distribution (?)

Line 876: “the developed insertion lateral relief offers a greater surface for extensor muscles of the digits (Guérin, 1980).” – as mentioned above, only the lateral digital extensor and (possibly) the radial carpal extensor pass over this section of the radius; the common digital extensor does not interact with this portion of the radius (as suggested by Guerin 1980). I realise that this is not in agreement with the cited literature; as a compromise, may I suggest the following: “the developed insertion lateral relief offers a greater surface for digit and carpal extensor muscle attachment (Guerin, 1980)”

Line 881-882: “The medial development of the olecranon process is related to larger insertions for the mm. flexor carpi radialis,” – I see here that my previous comment was incorrect. The flexor carpi radialis does not originate on the olecranon, the flexor carpi ULNARIS does. My apologies!

Line 966-969: “As bone size and body mass are intimately entangled (Berner, 2011), the centroid size of isolated bones may still constitute a useful body mass approximation when precise body mass remains unknown and if considered cautiously – this approximation depending on the number and placement of the landmarks on the bone.” – I agree. I will take this opportunity to direct the authors toward my own study from 2018 as an example of bone centroid size correlating with body mass, investigated with respect to GM of appendicular bones.
Reference: MacLaren, Hulbert, Wallace, Nauwelaerts (2018) A morphometric analysis of the forelimb in the genus Tapirus (Perissodactyla: Tapiridae) reveals influences of habitat, phylogeny and size through time and across geographical space. Zool J Linn Soc. 184, 499-515.

Line 982: “Limb straightness can results from the reorientation” – either “can result from” or “results from”

Once again, I congratulate the authors on the work they have done here, and I look forward to seeing this article published in PeerJ. I wish the authors the best of luck with corrections.

All the best,
Dr. Jamie MacLaren


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: INTERSPECIFIC VARIATION IN THE LIMB LONG BONES AMONG MODERN RHINOCEROSES—EXTENT AND DRIVERS
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors have incorporated all the feedback from the previous round of reviews. The paper is clear and unambiguous, with precise anatomical terms relevant to Rhinocerotidae. The literature and references provide appropriate and sufficient contest, with a clear professional structure. The R Script is clear and readable, and clearly correlates with the raw data. The paper is self-contained, well written, and a clear organization.
Experimental design: The experimental design is clear and expands upon accepted geometric morphometric data collection and analysis. No one has ever made as detailed a morphometric analysis of extant rhino anterior and posterior stylopod and zeugopod bones. Data analysis is clear and the methods are described in sufficient detail to replicate.
Validity of the findings: The findings are valid and carefully considered by the authors. A study on the exact same specimens would be easy to plan with the information given in this work. The paper also clearly adds to modern rhino morphological and functional studies, as well as fossil rhino studies. Habitat as a variable is carefully considered and found to be inconclusive, which is also an important benefit to the literature.

All underlying data have been provided and are statistically sound and controlled.

The conclusions are well stated and link directly to the original research question. Any speculation is clear.
Additional comments: Thank you for allowing me to read and edit this wonderful paper. I am so happy it is resubmitted. It is much stronger now and I was genuinely intrigued while reading the entire piece. I can't wait for it to come out so I can share it with my colleagues.

All the best.


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: INTERSPECIFIC VARIATION IN THE LIMB LONG BONES AMONG MODERN RHINOCEROSES—EXTENT AND DRIVERS
Review round: 2
Reviewer: 3

Output:
Basic reporting: The revisions by the authors satisfy my few concerns regarding the original submission.
Experimental design: The revisions by the authors satisfy my few concerns regarding the original submission.
Validity of the findings: The revisions by the authors satisfy my few concerns regarding the original submission.
Additional comments: The revisions by the authors satisfy my few concerns regarding the original submission.


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: EFFECT OF ORIENTEERING EXPERIENCE ON WALKING AND RUNNING IN THE ABSENCE OF VISION AND HEARING
Review round: 1
Reviewer: 1

Output:
Basic reporting: No raw data and data processing (i.e. codes) have been provided in the Supplementary files, I wonder if it would be possible to provide raw data, codes, and documentation that makes interpreting these data (or performing future analyses) easier for readers.
Experimental design: Introduction
How the results of this study add more insight in the field and how the results can be used in practical? Would be possible to clearly mention this in Introduction that make this paper more interesting.
Material and Methods
Line 155:I didn’t understand why 5 minutes and 2 minutes were used for walking and running tests, respectively.
Line 164-166: This kind of instruction influences the calculated variables (i.e. covered distance, angular orientation, and speed). The space should be big enough and without any obstacle, but apparently it was not.
I didn’t understand how and why the coordination tests have been performed and how the data has been obtained from these tests. The coordination tests and related data processing need to be fully described.
Statistical analyses
It was unclear to me exactly which statistical tests were used to compare walking and running, men and women, Foot_o and T& F groups, and to correlate between lateralization and the results of walking and running. I would suggest you to explicitly mention which statistical method has been used for which.
Results
Line 199-205: No p-values have been reported here.
Too much information has been shown in Table 1, 2,3, and 4. It is hard to reader to understand these results. I would suggest you to show these results in figures, rather than tables.
Discussion
It has just been mentioned that the results are consistent or contradict with previous studies and the paper has been stopped in this point. For example in Line 349, it has been mentioned that the results are contradict with Bracha et al.. Why the results are contradict? Not only it is important to mention consistency and contradictory, but also it is important to mention that why and how the results are consistent and contradict.
In the Discussion section the authors mostly described results. The usefulness of the findings was missing.
Lines 281-282: It is important to know how you ended up with this statement. Which task you mean? Based on which results Foot-O had much greater angular deviation than T &F? Please clearly mention the task and refer this statement to the related results that has been presented previously and follow this through the whole discussion. After showing the results in figures, I would suggest you to explicitly draw a link between Discussion section to Results section.
Line 301: How the diameter has been calculated? Please clearly mention this in Method section.
Validity of the findings: Too many statistical tests have been done without correction. In some cases the statistical test has been performed on very small sample size, such as comparison between men and women (N=5). Therefore, these statistical tests are most likely underpowered and the probability of type I error with such a small sample size is very high. I would suggest you to perform correction tests and take out all the statistical and correlated results about men and women from the paper.
Sample Size -- Line 127: No a priori power analysis presented for sample size of N=11 in each group. Given the relatively small sample size and multiple comparisons, please consider that the sample size needs to be fully justified and increased as needed to ensure rigorous and reproducible findings.
It was unclear to me how the authors calculated the variables such as covered distance, angular deviation, and speed in walking and running. I would suggest you clearly mention the data have been obtained from instruments, and the data processing has been used to exclude the aforementioned variables.
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: EFFECT OF ORIENTEERING EXPERIENCE ON WALKING AND RUNNING IN THE ABSENCE OF VISION AND HEARING
Review round: 1
Reviewer: 2

Output:
Basic reporting: The English language should be grammatically improved to ensure that an international audience can clearly understand the text. Some examples where grammatical or wording errors occur include lines 50 (“Human moving in space has been examined…”), 60 (“at a certain time”), 62 (“human moves”), 72 (“shown that human is able”). Throughout the text, I have highlighted examples in yellow.
Line 71 “or to 20 m (Souman et al., 2009) and eventually return to the same place” is not sufficiently clear. Is this a go and return task?

The sentence “Men, with domination of the left cerebral hemisphere (right-handed, right-legged and right- eyed) turn more to the right than to the left, while women, relying more on the right hemisphere, turn more often to the left than to the right” needs a reference. Moreover, the current phrasing makes comprehension difficult as it incurs that all women rely more on right hemisphere. Whereas hemispheres do work differently in the human brain, gender-brain differences are questioned in neurosciences and recent fMRI data points otherwise. See Nielsen et al. (2013) and follow literature thereafter.

On line 102. The paragraph ends with “These inconveniences can be minimized by practicing orienteering”. The sentence is not clearly linked to the paragraph because it assumes the reader knows which the inconveniences within the many arguments are. I suggest rewriting the paragraph with a direct flow of arguments, in consistent order. Currently, the arguments are ‘going back and forth’.

The research question is well defined and the approach of interest. However, the knowledge gap it aims to cover is not fully clear to the reader. The authors address it in disperse fragments within the introduction. Nevertheless, the reader does not find a cohesive fragment that highlights this point. Since so many of the citations have covered a similar field of knowledge, it is difficult to pin point where this article brings something unique to the field.
Experimental design: The participant consent is not in English. So I cannot review on that. This is ok. I understand translation might be troublesome. But I urge authors to consider any inputs given by reviewers who speak polish.

The researchers should clarify where is Lower Silesia region (country?).

Lines 133-135 present results not methods.

Are “sound-absorbing headphones” the same as noise cancelling headphones (line 157)?

What was the location precision of the GPS device in terms of meters? I understand it has high recording frequency (that is an important report), but its precision is also relevant to this experiment. Moreover, the high frequency was probably used for correction of error points? If so make this available to the reader. i.e. If a point was further than xx it was considered wrong data.

What is the threshold to define when a participant starts moving in a circle? (line 191)
Validity of the findings: I understand that gender had an effect on the results. This is an important aspect which the authors address. However, I miss a stronger argumentation regarding the fact that spatially trained athletes did not differ from non-trained ones. Why isn’t that more highlighted in the discussion? I believe it is an interesting factor. If not explained by lateralization than why would we not be “wired” to move in straight lines? Or is direction of movement very dependent on sensory input/ references? Speculation is welcomed.
Additional comments: Results
Figure 1 is good for the data was transformed to aid interpretation, but the graphics of the image are not at a high standard. The colour code does not facilitate for the discerning between T&F and Foot-O groups. On the legend the sentence “because of stopping the participant before the obstacle” is unclear.

Line 199 to 202 have repeated text?

Table 1 (S1) contains important information but does not follow publication standards. Thereafter it is unnecessarily hard to read through. This visual aspect should be improved in all tables within the article. See as an example:
https://dl.sciencesocieties.org/files/publications/style/chapter-05.pdf

Discussion
Line 277: Considering that no significant differences were observed in the running test. I wonder, since participants where not moving at max speed during walking, why would sexual dimorphism play a role on the results?  Or are the authors claiming that anxiety levels differ between genders? And if anxiety differs, why did it not affect the running speed?

The discussion fragment is relevant, but the flow is considerably hard.

Conclusion
Line 365-366: I understand what the authors mean, however the text per-se is unclear. -> Applies to experts when those are deprived of vision and hearing.


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: MICROBIAL COMMUNITIES ASSOCIATED WITH THE BLACK MOREL MORCHELLA SEXTELATA CULTIVATED IN GREENHOUSES
Review round: 1
Reviewer: 1

Output:
Basic reporting: In some cases  The MS does not meet all the required standard of the Journal from editing point of view.
1. Line numbers are missing.
2.	The MS font is not unified.  It is written in tow mixed fonts along the MS (Ariel and Ariel Unicode).
3.	The citations within the MS are not written in the same font, some with italics and some are not.
4.	The scientific names should be marked (italics) also in the list of references.
5. 	There is mixed used between stem and strip terms describing the same organ (stipe in text and stem in figures). Should use the same word.
6.	Figure 3: What are represented by stem 7,3,2,8    and Stem 5,9,6,1,10 and the two groups of cups? Are they stems and cups of young and matured mushrooms? While the tow stem groups seem to be different in their prokaryotic profiles in the figure, there is no indication clarifying in text what they represent.
7.	Fig 1:You have mentioned in the legend that fungal results are of fruiting bodies while in text you describe it as soil substrate samples.
8.	Reference list: the references of Masaphy,S, 2010 and of Volk TJ, Leonard TJ. 1989 are found in the reference list, but are not mentioned in text. Please add them as citation in text.
Experimental design: No comments
Validity of the findings: No comments
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: MICROBIAL COMMUNITIES ASSOCIATED WITH THE BLACK MOREL MORCHELLA SEXTELATA CULTIVATED IN GREENHOUSES
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: This study reported the microbiomes associated with the growing and fruiting of Morchella sextelata. The experiments and bioinformatic analyses were nicely conducted, and presented with enough details. The findings are novel, and add important knowledge into the environmental mechanisms triggering morel fruiting.

The manuscript is well written, but could be improved to a better quality by polishing some details in the wording and figures (see below). The order of some sentences could be adjusted to make the language more fluent. Basically it could be accepted after a few minor revisions.

Title:
“Morel mushroom” sounds a little weird. “Morel” means Morchella mushroom, so “morel mushroom” is like “chicken animal”, sounds redundant. A single word “morel” or “morels” is enough.

Abstract and main text:
Avoid to use too much “we”, “we found”, “we use”, etc. Passive sentences are better for describing the methods and results. Same to the main text. “Growhouse” should be “greenhouse”?

Pileus or cap, stipe or stem, should be used uniformly all through the article. Some figures used “cap” and “stem” while other places used “cap” and “stipe”. These are suggested to be uniformly corrected to “pileus” and “stipe”.

I polished the abstract as an example:

Morels (Morchella spp.) are iconic edible mushrooms with a long history of human consumption. During the fruiting course of morels, some microbial taxa are believed to be important for triggering the formation of primorida and development of fruiting bodies. Thus, there is interest in ecology of microbiomes associated with the morel. In order to identify and compare fungal and prokaryotic communities presented in the soil substrates locate in outdoor greenhouses where Morchella sextelata is cultivated, metabarcoding surveys of ITS and 16S amplicons are used. The results show that Pedobacter, Pseudomonas, Stenotrophomonas, and Flavobacterium comprise the core microbiome of M. sextelata. These bacterial taxa were also abundant in substrates beneath growing fruiting bodies. Twenty-nine bacterial taxa were statistically associated to Morchella fruiting bodies. The prokaryotic community network analysis revealed high modularity with OTU clusters such as (???, ???, ???) living in specialized niches (e.g. pileus, stipe). The soil mycobiome beneath morels was dominated by Morchella, Phialophora, and Mortierella. This research improved our understanding of microbial indicators and potential facilitators of Morchella fruiting body production.

Figures:

The figures are nicely drawn but the tags and labels could be polished to facilitate the readers understanding precisely. "Mature" to  "Mature fruiting bodies". "Young" to "Young fruiting bodies". "Cap" to "pileus".
Captions of Fig. 1,3,4,5, and Table 2, are incomplete. These errors need correction.


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: MICROBIAL COMMUNITIES ASSOCIATED WITH THE BLACK MOREL MORCHELLA SEXTELATA CULTIVATED IN GREENHOUSES
Review round: 1
Reviewer: 3

Output:
Basic reporting: no comment
Experimental design: The sampling method needs more detail. I suggest that you improve the description at line 100-108 to make the procedure repeatable.

For comparison, i think the soil sample with no fruiting bodies should be collected and analyzed.
Validity of the findings: In line 353, you concluded that " many microbial taxa appear to be unique to morchella". I would say that  if the result obtained from the samples collected at more sites ( only one site in this work ) could be more convincing.
Additional comments: Recent years, morels are widely cultivated in non- axenic soils in China. The results of this work add the evidence that morel plays a role in the selective inrichment of specific bacterial taxa, which is important to understand the soil microbial niches for the morel growth. It also has practical implications that specific bacteria could be used as promotor for morel production. Because the results that you obtained were from only one sampling site, i suggest that the title of this paper should be " preliminary study of microbial communities associated with morel (morchella sextelata) mushrooms cultivated outdoors.".


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: MICROBIAL COMMUNITIES ASSOCIATED WITH THE BLACK MOREL MORCHELLA SEXTELATA CULTIVATED IN GREENHOUSES
Review round: 1
Reviewer: 4

Output:
Basic reporting: As for the language, there are no comments. It is suggested only to check if "cooccurrence" should be written all attached or not. In the text it is written in both ways (line 166, line 584,586).
In the abstract, line 33 it is not clearly described whether the findings are in the Morphella carpophore.
Furthermore, in the abstract it is not clearly explained whether the fungal populations were also searched for in the Morchella carpophores, since in the abstract we speak only of soil.
Regarding the references, they are certainly complete and up-to-date, nevertheless, important European works on the truffle are absent, line 293 and 294. For example Amicucci et al 2019, Barbieri et al 2007.
One observation: why in line 93 states that the authors hypothesize the presence of pathogenic bacteria? and why then in line 313 is it stated that "surprisingly" pathogenic fungi have been found? Explain this point better.
Regarding the structure of the work, there are small imperfections to be checked. In particular the font size is different. Check lines 144-146, 216, 259-265, 568-569, and also in the rest of the text.
The figures are fine, they are almost all clear, with some exceptions. The caption of figure 1, line 568-569, does not mention that 1B refers to bacteria. Obviously, looking at the diagram and the list of phylums you can guess. For clarity, the authors could add in the diagram "Fungal Family" in figure 1A and "Bacterial phylum" in 1B.
Still referring to figure 1, and to the results it exhibits, it is not explained either in the figure or in the text, why the authors decided not to analyze the fungal population in the different tissues of the fungus, as instead was done for the study of bacterial populations. Still referring to this experiment, it is not explained why the study in the different stages of maturation was not done for the bacterial analysis such as for fungal analysis.
Experimental design: The experimental design is well done and structured, even if the classification of microorganisms remains at the level of genus and not of species. Some small improvements can be made. In particular line 103-104, it is not described how the degrees of maturation of the samples under analysis were defined, nor what the degree of maturation to which the analysis took place. In the paragraph that describes the sampling, line 108, we suggest to define better what it refers to when writing that 40 samples have been analyzed in all.
We also suggest to write more clearly the procedure of concentration and preparation of amplicons, line 116 and later. Were the bands excised and purified by gel?
In line 117, explain why the 15% influence on the migration of ethidium bromide does not affect subsequent analyzes.
The conclusions are appropriate; a summary table would certainly be very interesting with a comparison of the microbial populations among the various fungal species analyzed in the literature, although not necessary for the purposes of publication.
Validity of the findings: no comment
Additional comments: No additional comments


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

Input:
Title: MICROBIAL COMMUNITIES ASSOCIATED WITH THE BLACK MOREL MORCHELLA SEXTELATA CULTIVATED IN GREENHOUSES
Review round: 2
Reviewer: 1

Output:
Basic reporting: Need more attention in regard to editing materials such as fonts and line spacing, addition of some data concerning the methodology, and little more in-depth discussion to compare this work to previous work on similar topic.
Experimental design: suggesing to write  a little more in-depth discussion to compare this work to previous work on similar topic, i.e. on cultivated Morchella  (Liu et al 2017).

Methods - need to add some small detailes
Validity of the findings: The findings are intersting and all data have beedb provided.
To my opinion, the autors need to give more larification regarding the different in the aim and in the results from previous work done on Morcheela (Liu et al 2017)
Additional comments: Generally, this version of the MS is much improved, and it obvious that the authors maid efforts to reply.
However, unfortunately, some of earlier comments were not treated.
Here are some of earlier comments and new ones. Hope this will improve the published MS.
My suggestion is that the MS will go through a professional paper editing to avoid these small writing errors.

Line numbers are according the word TrackChange file.

Old comments:
1. The MS font is still not unified. It is written in tow mixed fonts along the MS (Ariel and Ariel Unicode).  See for example lines 171-174, 245-247 ect. Also line spacing is not unified.

2. Reference- the scientific names are still not marked (italics) in the list of references.

3. There is still use of the words we in many occasions along the MS. Please avoid the use of we, "we hypnotize" ect. It is suggested to use   "it is hypnotize"

New comments:
1. Abstract: line 40, please add "beneath growing fruiting bodies" after the word soil, as you have not analyzed or any soil or substrate, but soil beneath growing fruiting bodies in particular.

2. Methods: Line 120- please add "beneath growing fruiting bodies" after the word "soil"
3. Methods: line 127- There are 30 samples and not 20.
4. Methods : Line 134- You have mentioned how the soil DNA was extracted      " DNA was extracted from ~0.5 g of dried and homogenized soils with the PowerMag®" , but no indication of how the mushroom parts were treated, and DNA extracted.

5. Introduction and discussion:  please indicate what the different between the current work and the work of Liu et al. 2017. Is it only the outdoor and greenhouse cultivation? Is it the mushroom species? Is it the mineral that are used? Are the mushrooms in the current work had any enrichments by minerals? There is no discussion on the overall differences between the origin of the samples and also not so much on the differences of the results if any?


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: MICROBIAL COMMUNITIES ASSOCIATED WITH THE BLACK MOREL MORCHELLA SEXTELATA CULTIVATED IN GREENHOUSES
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The authors have made satisfactory improvements to the manuscript. It can be accepted almost as it is, except that I still have two suggestions below. I trust that the authors can address the minor changes by themselves so that I don't request to see the revised manuscript again.
1. "Morels" usually means a community of morels consisting of different species. When referring to only Morchella sextelata, "a morel" is more accurate. Please revise this issue in the title as well as other places in the article.

2. Consider using "mycosphere soil" instead of "soil beneath the fruiting bodies". Define "mycosphere soil" as "soil beneath the fruiting bodies" at the first place it appears (and citation, doi: 10.1093/femsre/fuy008, Bacterial–fungal interactions: ecology, mechanisms and challenges), then use "mycosphere soil" afterwards althrough the article.


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 RELATIONSHIPS BETWEEN BILINGUAL LEARNING, WILLINGNESS TO STUDY ABROAD AND CONVERGENT CREATIVITY
Review round: 1
Reviewer: 1

Output:
Basic reporting: It is a very interesting article, which addresses a topic of interest such as creativity. However, there are some suggestions that should be addressed before the article is published.

In the introduction, the authors pose the case of Rohan as an example of experience to sustain the importance of cultural activities. The case is interesting, but as stated, it is not possible to establish scientific sustenance.

In the introduction the authors suggest that a stable income is necessary to study abroad, however, the design of the experiment does not clearly control this variable. The inference of the concept is not clear.

They also infer that people study more and more abroad or plan to study abroad for further studies, but this inference lacks scientific support in the article.
Experimental design: As an objective it is indicated that the study seeks to measure the impact of bilingual learning and the willingness to study abroad on convergent creativity. However, I believe that the results of the objective have not been explained clearly. The analyzes show significant differences between groups and correlations, but I have not been able to visualize the impact indicated clearly. The discussion starts with: This research showed that bilingual learning was positively correlated with convergent creativity performance, that is, correlation and not impact. Even when a procedure of mediating effect is established, there are doubts about the application of the methodology.

The use of Bootstrap of 5,000 samples is proposed to measure the effect. However, the method, the technique used, the software, are not presented. It seems to be a PLS analysis, with which the model must report what is indicated in the literature regarding the validity of measurements and the model. There is a lack of information to clarify the technique.

It is not indicated in the procedure who and what the Bilingual Proficiency and Overseas Experience Questionnaire was used for. It must be explained in more detail.
Validity of the findings: The Cronbach's alphas of the PA and NA subscales were 0.28 is a value that must be explained.

When the technique used for mediation is indicated, the analyzes must be reported to validate said results.
Additional comments: In a very interesting article. But I feel that there is a lack of background in its presentation for its final publication.


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

Input:
Title: THE RELATIONSHIPS BETWEEN BILINGUAL LEARNING, WILLINGNESS TO STUDY ABROAD AND CONVERGENT CREATIVITY
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript studied the impact of willingness to study abroad and English proficiency on students’ convergent thinking performance. Moreover, the relationship between willingness to study abroad and RAT performance was found mediated by second language proficiency.
Overall, the study investigated the relationship between bilingualism and convergent creativity from a novel perspective that could be of general interest in the field of pedagogy and psychology. The results are interesting and worth to be published.
Experimental design: While the study design is quite simple and straightforward, more explanations on the following issues are necessary:
1. In the introduction, the author provided evidence for how multicultural experiences can make a difference in individual creative ability. However, it should be noted that there is a gap between the experiences and willingness to studying abroad. Therefore, the fact that multicultural experiences improved creativity is not sufficient to support the hypothesis that willingness to study abroad can improve creativity. Although the author suggested that the difference in willingness might reflect a difference in openness, the reason for involving the willingness to study abroad in the current study should be discussed more explicitly with more empirical evidence.
2. Please provide a descriptive result about RAT performance, monthly household income, and bilingual proficiency.
3. In the method section, information about the measurement of monthly household income is needed.
4. It should be “PA” instead of “PN” in line 282.
5. The importance of SES was discussed in the introduction, however only the mediating effect of second language proficiency was analyzed. Why not take the mediating effect of monthly household income into consideration?
Validity of the findings: 6. In the conclusions section, it was mentioned that “education policies should focus on cultivating students’ English proficiency and increasing opportunities for students to study and work abroad because these are effective ways to improve students’ convergent creativity”. Considering the quasi-experimental design of the current study, more experiments should be done before drawing this conclusion.
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 RELATIONSHIPS BETWEEN BILINGUAL LEARNING, WILLINGNESS TO STUDY ABROAD AND CONVERGENT CREATIVITY
Review round: 2
Reviewer: 1

Output:
Basic reporting: I have reviewed again and I think there are some minor adjustments that the authors must incorporate before the article is published.

These are detailed below:
The introduction has been strengthened, but now I miss incorporating a section in which each of the hypotheses that we want to support is discussed. It is necessary to order the introduction and relevance of investigating the topic and the existing gap. But they are confused with the hypotheses. In the discussion these sections are very clear, I recommend doing this in the introduction. This will strengthen your work.
Line 110. Most studies are indicated, however, only one study is referenced. They must improve that phrase.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The document has improved greatly since its last presentation. I thank the authors for the effort to improve their work and take into account the observations.


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 RELATIONSHIPS BETWEEN BILINGUAL LEARNING, WILLINGNESS TO STUDY ABROAD AND CONVERGENT CREATIVITY
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: All my concerns properly addressed, no further comment. Acceptance is suggested.


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

Input:
Title: TRANSCRIPTOME ASSOCIATION STUDIES OF NEUROPSYCHIATRIC TRAITS IN AFRICAN AMERICANS IMPLICATE PRMT7 IN SCHIZOPHRENIA
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: The main issue in the experimental design is that the Bonferroni correction was calculated accounting for the number of models tested in each tissue, but the correct multiple testing correction was supposed to account for the number of models and the number of tissues tested. My suggestion is to use a false discovery rate approach to account for the correlation among the tests conducted.

It is nice to see that the authors investigated the concordance between GTEx v6 and v7. However, it is also confusing. GTEx v7 includes a larger number of individuals and it should be a more powerful dataset. My suggestion is to consider GTEx v7 as the primary dataset and include the comparison with GTEx v6 as a reliability check.

Additionally, there are two main limitations that the authors should at least acknowledge:
1) GTEx includes mainly individuals of European descent and the use of this dataset is surely not optimal to predict the transcriptomic profile of African-American subjects.
2) African-Americans are a recently-admixed population and their genetic background is a mosaic of African and European haplotypes that can be very different among individuals included in this ethnic group. Principal components are likely not enough to account for the local ancestry diversity among the African-American individuals investigated.
Validity of the findings: The authors reported seven genes. However, with the exception of ZNF562 (Brain Cerebellum-V6), the predictors identified are mostly related to tissues that are not likely to be involved in the pathogenesis of psychiatric disorders. This may be explained by the incorrect multiple testing correction. The authors should justify better the biological meaning of the tissues identified with respect to the disorders investigated.

It is also hard to follow whether the gene-tissue combinations identified actually replicate in the European-ancestry dataset. For example, Figure 3 does not show the direction of the associations.

An additional suggestion is to conduct a trans-ancestry meta-analysis between the African-American and European-ancestry datasets to uncover additional genes that may be shared between these ancestry groups.
Additional comments: Investigating diverse ancestry groups is a priority in human genetic research. The present manuscript surely contributes to this important goal. However, there are several major issues that the authors should address.


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

Input:
Title: TRANSCRIPTOME ASSOCIATION STUDIES OF NEUROPSYCHIATRIC TRAITS IN AFRICAN AMERICANS IMPLICATE PRMT7 IN SCHIZOPHRENIA
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall, this paper is structured reasonably and written clearly. However, some places are a bit tricky to parse and methods could be expanded upon. An example of a tricky to parse place: the choice of reference panels for imputation is a major consideration for diverse populations, and the authors appear to attend to this, although the phrasing of the relevant sentences is not fully clear. Specifically, which reference panel was used for imputation? The relevant sentences conflict with each other on lines 106-109. I believe the authors mean 1000G was used for phasing followed by CAAPA for imputation? The latter would be a much more appropriate fit for imputation, as it is more ancestry-matched.
Experimental design: 1. Could the authors clarify why they chose to include expression models based on tissues not from the brain for these two mental health phenotypes? It seems challenging to interpret why expression changes in other some of the other organs identified could be related to neuropsychiatric phenotypes. Restricting to only nervous system derived tissues would have decreased the multiple testing burden / reduced concern over irrelevant/false positives associations.

2. Expanding on my concern over false positives: the authors do not currently have a detailed discussion of explicitly how multiple testing was addressed. This is key, as many tests for the same phenotype were run across many tissues in multiple datasets, some of which the authors note had differing significance thresholds within them, which reads as though a 5% significance threshold allowed in each. I did not see specific discussion of controlling for false positives across the 4 datasets further. The additional concern for the potential of false positive associations due to the admixed nature of these subjects plus the ancestry mismatch between the expression data and individual data means this is especially key to control for.
Validity of the findings: I would appreciate a further discussion regarding the many associations obtained in the PrediXcan that did not replicate [paragraph starting on line 177]. I appreciate that this is an understudied population which may have some ancestry-specific hits, but 5 out of 7 hits not replicating with any published research seems striking. What is the authors’ explanation for this result and justification that these are not false positives?
Additional comments: This paper takes a stab at starting to address a significant issue that plagues the GWAS community: the lack of diverse populations in psychiatric genetics research. I commend the authors for contributing to rectifying the underrepresentation of association studies on African American populations with this work. While most of their analyses are underpowered due to limitations of samples of relevant ethnicities, the overall workflow (QC, choice of analyses) appears generally appropriate. I do have some questions about technical specifics that I would like addressed, however, before I can recommend wholehearted acceptance of this paper, as detailed here. Specifically, I am not fully convinced that the genes highlighted by the expression scans are all truly hits relevant to the phenotypes of interest (especially given their lack of replication in much larger datasets) and would like the authors to fully convince me that there is no concern for false positives. Overall, while few significant results emerge from this paper, it is a commendable early attempt to address the disparity in association studies conducted on African American individuals.


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

Input:
Title: TRANSCRIPTOME ASSOCIATION STUDIES OF NEUROPSYCHIATRIC TRAITS IN AFRICAN AMERICANS IMPLICATE PRMT7 IN SCHIZOPHRENIA
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors adequately addressed my concerns.
Experimental design: The authors adequately addressed my concerns.
Validity of the findings: The authors adequately addressed my concerns.
Additional comments: The authors adequately addressed my concerns.


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

Input:
Title: TRANSCRIPTOME ASSOCIATION STUDIES OF NEUROPSYCHIATRIC TRAITS IN AFRICAN AMERICANS IMPLICATE PRMT7 IN SCHIZOPHRENIA
Review round: 2
Reviewer: 2

Output:
Basic reporting: The text on the x-axis of Figure 3 is very small and thus hard to read.
Experimental design: I am satisfied with the additional analyses to address my and the other reviewer’s concerns over multiple testing correction.
Validity of the findings: I have one remaining comment with regard to the presentation of the most significant SNP, rs10168049 – the authors should clarify their language to make clear that though this is the lead SNP, it is not necessarily the causal SNP. For example, on lines 227-229 in the Discussion they say “…its low minor allele frequency in European populations suggests that it could have a larger functional impact in African populations”. The notable feature of this SNP is that the larger MAF in African-descent populations lends it increased power to be significant in GWAS, but does not necessarily suggest that it has a bigger functional impact. It has a better ability to be identified, and thus opportunity to tag whatever is the true causal variant.
Additional comments: As noted in the last round of review, I appreciate the authors’ early contribution to rectifying the underrepresentation of genetic studies on non-European populations with this work. These new results appear a lot more robust and easier to interpret with the imposing of more stringent false discovery thresholds and after the removal of superfluous data.

In sum, while few significant results emerge from the reanalysis, I have much more confidence in the gene that did survive the false discovery testing. For this reason, I now feel comfortable recommending this paper for publication in PeerJ.


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

Input:
Title: COMPREHENSIVE EVALUATION OF FLUROXYPYR HERBICIDE ON PHYSIOLOGICAL PARAMETERS OF SPRING HYBRID MILLET
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper entitled “Comprehensive evaluation of fluroxypyr herbicide on physiological parametric in spring hybrid millet” describe the physiological and biochemical changes occurred in Setaria italica by the application of a hormonal herbicide (fluroxypyr). The importance of this paper designs a technical guide to the use of chemical control for this crop.

For this objective, the authors developed a very detailed study to measure these changes after the herbicide application (5 and 10 d). However, the introduction has critical and conceptual errors. The principal argument is the study of the resistance mechanisms in Foxtail millet. However, the resistance is caused by the repeated application of herbicides; in other words, is the result of a selection process. In this case, the term tolerance is adequate for the study. The Weed Science Society of America defines tolerance as “the inherent ability of a species to survive and reproduce after herbicide treatment. This implies that there was no selection or genetic manipulation to make the plant tolerant; it is naturally tolerant (Weed Technology 12(4):789, 1998). For this reason, the introduction and objectives are not congruent.
If authors can change the scope of the paper, this will be an important contribution to weed management.
Experimental design: the experimental design is adequate for evaluating the "tolerance" of Foxtail millet to the herbicide fluroxypyr. Several physiological parameters were evaluated and give a detailed description of changes occurs in plants.
Validity of the findings: 'no comment'
Additional comments: This is a good work. However, the introduction has mistakes in the concepts. If you can make the changes, this paper could be accepted whatever 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: COMPREHENSIVE EVALUATION OF FLUROXYPYR HERBICIDE ON PHYSIOLOGICAL PARAMETERS OF SPRING HYBRID MILLET
Review round: 1
Reviewer: 2

Output:
Basic reporting: In general, this work appears to be well conducted and presenter. However, my main criticism is the excesive wording in introduction and discussion.
Experimental design: Plase explain why is the recommeded dose is of 1 L/ha doses up to 4 l/Ha were used. Severe damage are expected under such treatments.
Validity of the findings: No comments. Just please, try to present them ia a succint way.
Additional comments: The work deserve publication, but it could be improved by shortening as suggested.


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

Input:
Title: COMPREHENSIVE EVALUATION OF FLUROXYPYR HERBICIDE ON PHYSIOLOGICAL PARAMETERS OF SPRING HYBRID MILLET
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript (ID: 34816) entitled " Comprehensive evaluation of fluroxypyr herbicide on physiological parametric in spring hybrid millet " is of high quality and suitable for publication in this journal, however it needs minor revisions.
This manuscript describes a study on the physiological reaction of different physiological parametric to the spraying of different dosages of herbicide fluroxypyr at the seedling stage of hybrid foxtail millet. Effects of an auxin herbicide, fluroxypyr, on growth parameters, photosynthetic status, and hormone status were examined. Among them, photosynthesis and hormone status (GA and ABA) were most sensitive. I evaluated the manuscript in two parts:
(1)	The language is not checked properly, there are frequent grammatical errors and language editing by special editor of native speaker.
(2)	The design, implementation and results: The manuscript has innovation but I do not understand what is the biochemical interpretation of the results of the statistical analyses. To be honest, I do not know if these methods are actually useful to address the resistance mechanism of this plant.
Experimental design: The authors treated foxtail millet with an herbicide fluroxypyr at various concentrations, and analyzed multiple aspects of the plant physiology. The plant not only showed enhanced and suppressed growth depending on the treated concentration, but also accumulated the reactive oxygen species, and showed enhanced enzyme activities that involved in the metabolism of reactive oxygene species. The treatment also affected various parameters concerning the photosynthesis and plant hormone levels. The design and results are feasible and reliable, which provide useful data for herbicide related research in foxtail millet and other crops.
Validity of the findings: It is well known that photosynthesis is very sensitive to any biotic and abiotic disturbances. In fact, photosynthesis is significantly reduced after treatment of any herbicides irrespective of their modes of action. Furthermore, as fluroxypyr is a typical auxin herbicide, increased ethylene biosynthesis and ABA accumulation shall be observed after fluroxypyr treatment. In general, auxin herbicides including fluroxypyr disturb auxin homeostasis and promote ethylene biosynthesis and accumulation of ABA, resulting in growth retardation and plant death. The design and result are generally fine, which provide useful data for herbicide related research in foxtail millet and other crops.
Additional comments: 1. The discussion is not sufficient and a bit rigid in terms of its structure.
2. Format: some refs are wrong in the names of Chinese authors, given names were used as surnames.
3. In line 71, whether the experiment was carried out in a laboratory or greenhouse?
4. The figures are not well organized. For example, in Fig. 1 the SOD activity is expressed as line graph, but the POD activity is expressed as bar graph. This is very strange because they are both enzyme activities. All of the figures should be modified in an appropriate way.
5. There is a grammatical error in the manuscript. Please check it by a native English speaker.


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

Input:
Title: COMPREHENSIVE EVALUATION OF FLUROXYPYR HERBICIDE ON PHYSIOLOGICAL PARAMETERS OF SPRING HYBRID MILLET
Review round: 2
Reviewer: 1

Output:
Basic reporting: This article had been revised previously. The conceptual errors pointed out by this reviewer have been corrected.
In my point of view, I consider that this article has already the required quality to be published in PeerJ
Experimental design: no comment
Validity of the findings: no comment
Additional comments: No additional comments


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

Input:
Title: COMPREHENSIVE EVALUATION OF FLUROXYPYR HERBICIDE ON PHYSIOLOGICAL PARAMETERS OF SPRING HYBRID MILLET
Review round: 2
Reviewer: 2

Output:
Basic reporting: All of my comments were properly adressed in this new version. In fact, I consider that the new version shows a significant improvement from the previous one, after the reviewer comments.
Experimental design: No comments
Validity of the findings: No comments
Additional comments: Addressing the reviewers' comments resulted in a better organized and clearer paper.


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 REDISCOVERY OF THE RARE VIETNAMESE ENDEMIC ERIOPHORUM SCABRICULME REDEFINES GENERIC LIMITS IN THE SCIRPO-CARICOID CLADE (CYPERACEAE)
Review round: 1
Reviewer: 1

Output:
Basic reporting: .
Experimental design: .
Validity of the findings: .
Additional comments: The project was well designed, the results carefully analyzed and presented as concisely as possible and the significance made clear.
See attached.


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

Input:
Title: THE REDISCOVERY OF THE RARE VIETNAMESE ENDEMIC ERIOPHORUM SCABRICULME REDEFINES GENERIC LIMITS IN THE SCIRPO-CARICOID CLADE (CYPERACEAE)
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is well written and structured, with all sections in clear professional English. The authors refer to relevant literature and provide detailed context were needed e.g. explaining application of place names in Vietnam. Sequence and occurrence data used are shared as supplementary files and info is provided on where the studied herbarium specimens can be accessed.
Experimental design: The data and methodology used are suitable for the answer the posed question on the phylogenetic position of the studied species. This study is part of research focused on the Scirpo-Caricoid Clade of Cyperaceae by the authors and contributes to a better understanding of generic limits in this group.
Validity of the findings: Data and methodology are sound. The conclusions are solid and based on the presented results.
Additional comments: There are a few small corrections to made (see the annotated PDF in 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: THE REDISCOVERY OF THE RARE VIETNAMESE ENDEMIC ERIOPHORUM SCABRICULME REDEFINES GENERIC LIMITS IN THE SCIRPO-CARICOID CLADE (CYPERACEAE)
Review round: 1
Reviewer: 3

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: The authors present the rediscovery of an "Eriophorum" species narrowly endemic to an ~200km area of Vietnam. Using a combination of morphological, embryological, and molecular data, they demonstrate that this species is nested within Trichophorum and is only distantly related to Eriophorum. Based on this evidence, they transfer the species to Trichophorum scabriculme.

This is by far the easiest review I have ever conducted. The writing is clear, the evidence for their results is overwhelming, the figures are helpful, and the species descriptions and key are thorough and useful. My only suggestion for improvement is that the overall length of the manuscript can be reduced significantly. I appreciate that the authors provide such a thorough context for the taxonomic delimitations of this these clades, but I found it to be unnecessarily long - and, much of it is rehashed again in the Discussion. Similarly, the phylogenetics section could be reduced - this is essentially the same tree, using the same molecular markers, that the authors have now published a number of times. A simple acknowledgement that the topology is consistent with their previous studies, and a brief mention of the placement of T scbirculme, could be sufficient.


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 REDISCOVERY OF THE RARE VIETNAMESE ENDEMIC ERIOPHORUM SCABRICULME REDEFINES GENERIC LIMITS IN THE SCIRPO-CARICOID CLADE (CYPERACEAE)
Review round: 1
Reviewer: 4

Output:
Basic reporting: The manuscript is well written throughout.
Experimental design: The experimental approach is fully in line with current methodologies.
Validity of the findings: The findings are clearly presented and explained.
Additional comments: I look forward to seeing this in print.


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 EFFECTS OF GROWTH RATE AND BIOMECHANICAL LOADING ON BONE LAMINARITY WITHIN THE EMU SKELETON
Review round: 1
Reviewer: 1

Output:
Basic reporting: Even though crucial for this study, discussion of Lee & Simons, 2015 and Pratt et al. 2018 findings which both failed to find support for torsional resistance role in bone laminarity in birds (and bats) is largely (or entirely) missing from the MS. In case of Pratt et al. 2018, this can probably be attributed to this paper being comparatively new. However, it is surprising that the findings of Lee & Simons 2015 on bird bones, with both authors being coauthors on the current manuscript, is not regarded in depth. In any case, both papers are of crucial importance for the current study, and hence their findings largely contradicting the conclusions of the current study must also be addressed and included in the discussion.
Experimental design: A figure or an interpretative drawing of the cortex sampling areas, i.e. octants and placement of the sampling point and sample boxes shown on two representative bones for growth rate and biomechanics tests, respectively, would be needed for the readers to get a better visual idea, even if this figure is added as supplementary only.

Statistical procedures are not well documented and there is likely a terminological confusion between logistic regression vs linear regression on log-transformed data, but due to insufficient provision of methodological details of their statistical analyses I cannot be sure.
However, if the authors really meant “logistic regression” with application of the Wilson estimate for confidence intervals, then I cannot see how their data structure was suitable for performing such an analysis.

As far as I could look it up in statistics, logistic regression is a probability regression with binary response variables and its graphical representation is the classical S-shaped curve with an inflection point at 50% probability. The binary nature of observations in logistic regression is expressed as "failure" or "success", and the probability comes from an x times success out of n times try. The same goes for the Wilson estimate: it's a method for binomial proportional confidence interval calculation. So how could the authors apply this method on their laminarity index (LI) data which, even if ratio values, still represent continuous variables and not binary? I could see this work only if they e.g. define "success" as having LI above a certain level, and failure as finding LI below that level; this would provide the binary data structure required for logistic regression (i.e. proportion of LI above vs below the specified level).

However, the provided dataset and the resulting figures do not support such a data analysis setup, so I’m wondering whether the authors actually meant that they log-transformed the dependent (LI) or both, dependent and independent variables and did a simple linear regression on the transformed data? If yes, this must be corrected throughout the MS. Otherwise, providing details of how (and why) they could use a logistic regression for their non-binary data is absolutely necessary.

In any case, an additional table summarizing test statistics and their results would also be necessary.

In addition, the function for fitting the trend lines in Figs 3 - 5 is also missing and should be specified.
Validity of the findings: My concerns about their statistical approach is mentioned in the "experimental design" evaluation field. All uncertainties originating from the concerned analysis of the data may affect the results and conclusions based on them, so without the statistical procedure properly laid down I cannot judge whether their conclusions are supported by their data. Nevertheless, based on their plots of raw data (Fig 3-5), their major conclusions on the relationship between growth rate and laminarity, and between shear strain and laminarity seem to hold true.
Additional comments: I find this work very interesting and would like to encourage the authors for doing more research in this exciting direction, and once sufficient and robust dataset was collected and analysed on extants, to extrapolate their findings on fossil dinosaur - bird transitional taxa (as the authors themselves also pointed out in their MS).

However, besides the comments mentioned in the major 3 fields, I'd like to point out some smaller issues that should also be addressed for scientific completeness.

In Results:
1) Figure 4 shows fewer data points used to construct the fitted curve than actually available for wing bones based in Table 2.

2) A simple plot of laminarity indices including all studied elements per specimen for visual comparison of differences among elements and age categories would be very useful and informative about general vascular pattern distribution within the skeleton and during ontogeny.

3) Surprisingly, spatial distribution of different vascular orientations throughout the cortex is not reported here to any extent. A potentially consistent regional difference in vascular architecture with homologous cortical areas showing similar orientations but a high variance among different areas could result in high overall cortical variance in LI. However, this should be distinguished from high variance in LI originating from more irregular orientations with no location-specific patterning throughout the entire cortex. This would also be very important to look at from an evolutionary perspective, as one would expect that low to no functional selection pressure on wing bones would result in high and random variance in its histological features which would have to be clearly distinguished from a potentially high overall variance with regionally consistent patterning.

In Discussion
1) Some aspects and questions are left open. For instance, even if non-significant, there is a clear negative trend between growth rate and laminarity in all wing bones too, based on Figure 5, but this is not considered in the discussion.

2) They also mention a three times difference in recorded mass growth rates of emus between their study and Castanet et al’s (2000) but there is no detail on how they assessed growth rates in body mass for their own specimens and whether their method to do so is the same as in Castanet et al (2000). Furthermore, they don’t consider possible reasons for this significant difference in mass growth rates. E.g. was there any difference in the diet, climatic conditions, locomotor freedom, etc under which emu specimens used in the two different studies were kept? Or were they a different breed? This is important, as these unknown factors may not only influence growth rates, but could partially be directly responsible for the differences detected in the prevalence of bone laminarity.

You find further detailed comments in the attached annotated pdf.

In sum, I would recommend publication of this work after moderate/major revision.

Sincerely,
Edina Prondvai


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 EFFECTS OF GROWTH RATE AND BIOMECHANICAL LOADING ON BONE LAMINARITY WITHIN THE EMU SKELETON
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Dear authors
The Ms entitled "The effects of growth rate and biomechanical loading on bone laminarity within the emu skeleton" is an important contribution to our knowledge of the functional significance of bone histological variation.
In my view, authors have to deal with 3 issues in order to improve the quality of the Ms.
1. Biomechanics. Skedros and Hunt (2004) tested in the turkey ulna diaphysis whether the degree of laminarity correlate with site-specific differences in collagen fibre orientation in primary bone. They showed highly significant positive correlations between laminarity index and predominant collagen fiber orientation. This relevant contribution is not cited in the Ms under revision ! According to an increasing body of knowledge, it seems that the histological feature linked to (explaining) bone biomechanical properties is the orientation of collagen fibers, the orientation of vascular canals being an indirect proxy of them. Moreover, collagen fiber orientation can be conserved in the fossil record during hundreds of million years, allowing paleobiological inferences of biomechanical features. Why did you analyze vascular orientation instead of collagen fiber orientation?
2. Growth rate. According to the results obtained by the research team of Marotti (see for instance the review of Marotti, 2010), static ossification produces woven bone at high growth rate whereas dynamic ossification produces parallel fibered bone or lamellar bone at low growth rates. It seems that collagen fiber orientation (rather than vascular canals orientation) is linked to bone growth rate. Again, why did you analyze vascular orientation instead of collagen fiber orientation?
3. Integrative analyses. Authors analyzed separately the relationships between, on the one hand, bone growth rate and bone laminarity and, on the other hand, shear strain and bone laminarity. However, the explanatory variables bone growth rate and shear strain interact among them and the effect of this interaction on the response variable (bone laminarity) has to be taken into account using for instance multiple regression. Moreover, the effects of body mass and age must also be taken into account in these integrative analyses.
Please don’t hesitate to contact me for any clarification.
Yours sincerely
Jorge Cubo


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 EFFECTS OF GROWTH RATE AND BIOMECHANICAL LOADING ON BONE LAMINARITY WITHIN THE EMU SKELETON
Review round: 2
Reviewer: 1

Output:
Basic reporting: As far as I’m concerned, the revised manuscript of Kuehn et al. satisfies every point of the criteria of basic reporting set by Peer J.
Experimental design: I am not a statistician but as much as I can judge, the new statistical approach applied in the revised version is appropriately chosen for testing their hypotheses and analyzing such data.

However, I still have a question concerning the implied necessity of log 10 transformation of original explanatory variables before turning them into PCs, and some missing details that should be added for a comprehensible methodology.

The authors say: “To minimize this multicollinearity, the variables of mass, age, growth rate and shear strain were normalized with log10-transformation and transformed to principal components”

As I understand, it is frequently stated that PCA can be used to combine highly correlated predictor variables to resolve multicollinearity, and that's why you used it. Besides that multicollinearity is not really minimized but rather preserved / combined in the PCs, the current formulation sounds like normalization via log 10 transformation would also be a necessary step on the way to minimize multicollinearity among your different predictor variables, which is, I assume, not the case.
Also, whether log 10 transformation actually normalizes the data or not depends on the original data distribution because only certain distribution types, mostly log-normal distribution, can be normalized by log transformation. (see e.g. Feng et al. 2014). Did data distribution for all your variables indeed become normal after log 10 transformation?

Furthermore, although I didn’t find it specifically stated in the MS whether you used correlation or covariance matrix for your PCA (which should be stated), if you used correlation matrix which, concerning your differently ranged and scaled variables, is needed here, it already includes a transformation, i.e.  standardization to mean = 0 and standard deviation = 1. So why would you use an extra, log 10 transformation as input for PCA?

In sum, I don't understand why this log 10 transformation is necessary here? As much as I know, PCA does not require normally distributed data, and collinearity, which has a significant impact on the outcome of the PCA as well, cannot be canceled by log transformation of input variables. I may be wrong with all this, but I don’t think that log 10 transformation will ensure normal distribution of the resulting PC scores, either, and that the following beta regression, being an ML regression, requires normally distributed explanatory variables.
Besides this, such data transformations usually make biological interpretation of the analysis results as well as the relationships in the original dataset more difficult.

Please, explain why this step was deemed necessary and included in the analysis. On the other hand, if it wasn’t necessary, I suggest you use raw data of predictor variables as an input for a correlation matrix-based PCA. This would allow a better interpretation of the end results too, even if it does not change the outcome drastically (which it probably won’t but it may change significance levels of regressions).

Also, please provide R script and maybe also R output in SI showing parametrization and link functions used in your beta regression models, or alternatively add an SI table summarizing this information. As this method is not frequently applied in such studies, this information would help readers tremendously to comprehend and later also apply your procedure.
Validity of the findings: The results gained with the new statistical method and their interpretations are sound, their logical connection with the hypotheses raised are clear, and now are nicely put in the necessary context of previous studies.
Although I suggested that the analyses are rerun with raw data instead of log 10 transformed predictor variable values, if implemented, the main conclusions of this investigation will most likely not change (as opposed to the previous MS version which gave quite different results and interpretation with the other applied method).
However, as the significance levels can still change with non-transformed data, and hence the relative importance of the findings can shift, it is necessary that the authors either argue why log 10 transformation is necessary to be kept, or they rerun the analyses.
Additional comments: This revised version has greatly improved in all aspects, and I’d like to thank the authors for taking my comments on the previous version seriously. The MS reads smoothly and the entire story, including figures, is much clearer and logical.

I have only a few extra comments in addition to the ones mentioned in the major 3 fields that should also be addressed for scientific completeness. The smaller issues are indicated in the annotated pdf.

1)	In the discussion, regarding the bat humerus laminarity, you say: “…the bat humerus. The lack of laminarity in this (suspected) torsionally-loaded humerus is presumably due to the slow somatic growth rates of bats…”
This sounds a bit confusing to me, because above you related lower growth rates to laminarity, and here it sounds like laminarity was associated to fast growth, and hence absent in slow growing bats.
Furthermore, bat bone vascularity seems extremely low for a small mammal that otherwise shows high metabolic rates (when not in torpor of course) and, as far as I know, their growth is not outstandingly slow among mammals of their size. Hence, this pattern of low cortical vascularity (almost lizard-like) must be explained by other factors (which might well be due to that central artery that is not published unfortunately) than an extremely slow growth.
So I feel that arguing with the missing laminarity in bat bones is, in itself, misleading because the simple lack of or extremely low vascularity is not emphasized, although it’s very important in this context of discussion.
So it should be emphasized that bat bones are almost avascular in smaller species and have very sparse vascularization in larger species which makes bat bones hard to compare to the densely vascularized bird bones in general.

2)	Concerning wing bones and their relation to LI, in my opinion, the fact that you detected that "ontogeny-independent growth rate" which explained a considerable amount of variance in wing elements also supports the release of canalizing selection pressures on the wing bones. This could also be discussed in the Discussion part as well as in the Conclusion, if you agree with my interpretation on this.

3)	Please, also check your Tables in the annotated pdf where I indicated some missing data that need to be explained and some columns the meaning of which was clarified neither in the text, not in the table caption.

All in all, it is a very nice and useful study with very interesting findings.

Best wishes,
Edina Prondvai


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 INTERPLAY BETWEEN COGNITIVE TASKS AND VISION FOR UPRIGHT POSTURE BALANCE IN ADOLESCENTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: - It is strongly recommended to do an orthographic and grammatical review before it is printed. This is necessary not only to improve the quality of the manuscript, but also to avoid misinterpretations.
- The introduction should explain some topics in more detail (I have made several recommendations below, see the PDF-Data). The final part of the introduction should be restructured in order to present a more logical and clear sequence of ideas until the hypothesis is reached.
-Figure 2 and 3 should provide more information (see details in PDF)
Experimental design: - The research question is definitely an issue of relevance. However, in many situations -probably due to language limitation- it is not possible to identify important methodological issues, such as the hypothesis of the study.
- Some aspects about the methods were asked (see PDF attachment) in order to provide sufficient details and information for a future replication.
Validity of the findings: - The choice of the statistical tests is correct. However, regarding the Bonferroni correction, some information needs to be offered (see PDF attachment)
- Regarding the interpretation of the result, I believe it is correct, but it has been extrapolated. I made some comments about in order to help you and avoid problems with wrong comprehension.
Additional comments: The authors investigated the influence of cognitive tasks on balance control (quasi-static balance) in adolescents, when performing with eyes open and eyes closed. This is definitely an issue of relevance, since there are controversies in the literature about dual task balance tests performed during eyes-open and eyes-closed conditions. Despite presenting numerous methodological and language problems, the study has good potential. In this way, I would like to contribute with some suggestions.

Dear Authors,
I have read your manuscript and generally, the study was sufficiently adequate for publication taking into consideration aspects like experimental design and validity of the findings. However, I have made several recommendations in order to make this study clearer and to improve its quality. Furthermore, there are some questions I would like to see answered related to the study. I would also like to recommend the reorganization of some information according to each section (I have made several recommendations below for each specific section). Additionally, it is also strongly recommended to do an orthographic and grammatical review before it is printed. I have also noted some sentences or phrases that should be rewritten. This manuscript is short and to the point but I believe the discussion could be better structured.