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: CRYAB PREDICTS CLINICAL PROGNOSIS AND IS ASSOCIATED WITH IMMUNOCYTE INFILTRATION IN COLORECTAL CANCER
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors have analyzed data from multiple publicly available databases to investigate the role of CRYAB in human colorectal cancer, showing that while CRYAB expression is lower overall in CRC cells, relative CRYAB mRNA levels are inversely correlated with survival and that CRYAB expression positively correlates with immunocyte infiltration. The authors implicate methylation status of specific gene body loci as potential regulators of CRYAB expression levels. This work provides a potential for CRYAB expression levels to serve as predictive indicators of prognosis for individuals with colorectal cancers.

The paper would be improved with a more thorough discussion of CRYAB expression in colorectal cancer and perhaps in cancer in general- there is some information about CRYAB expression in multiple cancers in Figure1B, but especially with this included, a more thorough background in the text would be useful. It also would be worthwhile to discuss some of the work done by the Pingsheng Chen lab on CRYAB expression in CRC.
The writing throughout the paper also needs to be improved for clarity. In several sections there was some unclear or contradictory language such as in lines 112-113, 130-131, 168, and there is also a sentence which appears to belong in a paper investigating Girdin expression in hepatocellular carcinoma (line 96).

The paper would also be improved with more thorough and descriptive figure legends.
Experimental design: Overall, the manuscript would benefit from far more detailed information regarding how the data presented were obtained and analyzed- without that information it is difficult to adequately evaluate the experimental design. Additionally, there should be a date of access included for each piece of data.  When replicating some of the graphs presented in the paper, for example, I found that for Figure 4, there were several minor differences in Rho and p values (there were no differences for Fig 4 F-G) when I accessed the TIMER database, so those should be updated in the manuscript. The authors should also clearly note that these data AND the statistical calculations are from TIMER, and also do so where appropriate for other analyses performed. Of particular importance, in my opinion, is the addition of information regarding exactly how Gene Ontology and KEGG analyses were performed.  This may be easily inferred by a reader who has experience with Go and KEGG, but as someone who has not used these tools, I would have liked more detailed information.
Validity of the findings: My biggest concern with the paper is that in many cases correlation is used to make claims about causality that could only be determined with targeted work to test these hypotheses.

In many cases the authors conclude that CRYAB is exerting a biological effect based on simple correlation. For example, the authors state that, “expression of CRYAB *leads to* focal adhesion, PI3K-Akt signaling pathway, Human papillomavirus infection…. (line 181), which cannot be concluded from this analysis. The correlation of CRYAB expression levels and immune response in a complex biological environment is not sufficient to claim that CRYAB “plays a key role in regulating tumor immunology (lines 260-261)” or that “the relative high expression of CRYAB may be a potential mechanism of *CRYAB induced* colon cancer (lines 257-258)”. This is an interesting hypothesis worthy of further investigation, but the data presented here shows only a correlation and is not sufficient to draw these conclusions without some targeted work testing these hypotheses regarding CRYABs role in CRC.

I do agree with the authors that CRYAB expression levels could be useful in a clinical setting to potentially function as a prognostic indicator in CRC patients, and this work lays some groundwork for informing experiments to test how CRYAB may function on a molecular level in colorectal cancers. With revisions to some of the interpretation of these findings, this paper presents sufficient data for a publication; however, some further work investigating some of those claims would dramatically improve the paper’s impact.
Additional comments: Below are some comments on specific figures and how they may be improved:

Figure 1:
It is not clear why the authors chose to include figures (A and B) showing CRYAB expression levels in a variety of cancers rather than just COAD, since the paper does not address CRYAB expression levels in these other cancer types (many of which showing a significant change in expression levels compared to wild type).  Previous published work has also shown an increase in CRYAB expression levels in COAD cancer cells (Shi et al 2014) and this should be addressed. Figure 1 could be improved by changing the color scheme for either A or B, since red and blue correspond to expression level in A but not in B. Crucial information regarding how TCGA was used to generate these plots is missing and I could not easily find on the TCGA web portal how one might replicate these.

Figure 2:
1.	The exact source of these images is needed, including not just the data repository but also patient/sample number.  Additionally, the antibody used should be reported.
2.	The images themselves do not with any degree of certainty demonstrate that there is a difference in CRYAB protein levels between normal and cancerous tissue. This is further compounded by the issue of different cell morphology in cancerous tissue, making comparison difficult. While it is understood that the authors are limited by the data available in the Human Protein Atlas Project, without the ability to distinguish a change in staining levels within tissue from the same patient, these data are not conclusive.

Figure 3:
The plots would be improved with clear/more descriptive legends for each as well as an n value for each measurement. For the methylation data, none of these reach the threshold of significance; this would be more appropriately included in supplemental data and not the body of the paper.

Figure 5:
The legend indicates that purple circles represent meaningful correlations, however both on my monitor and printed, none of the circles are purple.

Figure 6:
It would be useful if these were grouped such that methylation loci correlating with increased CRYAB expression are together, and vice versa.


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: CRYAB PREDICTS CLINICAL PROGNOSIS AND IS ASSOCIATED WITH IMMUNOCYTE INFILTRATION IN COLORECTAL CANCER
Review round: 1
Reviewer: 2

Output:
Basic reporting: Abstract:

1.	Conclusion.CRYAB may be a potential tumor suppressor
gene of COAD. CRYAB may be a new potential therapeutic target and predictive biomarker
for CRC. CRYB likely plays an important role in immune cell infiltration.

a.	Please correct CRYB to CRYBA to be consistent.
b.	What does the abbreviation CRC mean? Is it the same as COAD?

Introduction:

1.	Add prevalence of the disease (how many people or percent of population affected in U.S.?)

2.	Line 49 domain, and a C-terminal domain[11]. The study report that CRYAB may trigger the EMT in
50 CRC by activating the ERK signaling pathway and is a potential tumor biomarker for CRC
51 diagnosis and prognosis[12].

Please expand on the rationale for studying infiltration of immune cells in COAD. Has immune cell infiltration been attributed to worse tumor progression?
Experimental design: Methods

1.	Please provide the methods for the immunohistochemistry that is presented in Fig 2.
Validity of the findings: Results:

1.	Line 103 In general, the RNA sequencing data of 306 samples from the TCGA database and detailed
104 clinical prognostic information resources have been included in our study.

What is meant by “in general”?

2.	Line 104 clinical prognostic information resources have been included in our study. All patients were
105 randomly divided into low expression group (n =153) and high expression group (n =153).

What is meant by “randomly divided”. Is the dividing into low and expression groups is based on the data of expression levels for CRYAB?  Were the levels rank ordered and then divided at the midline so as to get exactly 153 in “low group” and 153 in “high group”?  If so, this does not sound like a scientific approach. Please provide details on methodology.

3.	Line 107 (p=0.1695, 0.3418, 0.6467). M0, N0, and Stage I are different

What is meant by “different”? Please expand.

4.	Line 111 cancer (Figure.1A). TIMER analysis revealed the comparison of CRYAB gene among various
112 cancer types including colon cancer, and indicated that CRYAB of colon adenocarcinoma
113 Significantly down-regulated genes(Figure.1B).

Correct to “is significantly” ?

What genes are "down-regulated" exactly ? Please provide a line or two about this.

5.	Table 1: Is colorectal adenocarcinoma the same as colorectal neoplasm? Text talks about adenocarcinoma but table lists neoplasms.

Please be precise in table legend and write the location of the CRYAB expression  - presumably in the tumor ?

Also add to Table 1 legend what the abbreviations mean such as the Type N1, N2, T1, T2…

6.	Line 117 (Figure.1 F). We then performed a meta-analysis on the above three data sets to evaluate the
118 association between CRYAB gene expression and OS and obtain more objective conclusions.

What does the abbreviation OS mean?

7.	Figure 2:

The immunohistochemistry claim that CRYAB staining is increased in COAD is very unconvincing.
Please provide inserts of larger magnification and perform quantitation.
Can you identify what cells the CRYAB is expressed and increased in?
Additional comments: 1.	This manuscript provides potential interesting results regarding CRYAB as a biomarker of tumor progression in COAD.
2.	Please correct ‘nuetrophil’ spelling to ‘neutrophil’ thoughout the paper.
3. Manuscript could benefit from improved grammar.


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: CRYAB PREDICTS CLINICAL PROGNOSIS AND IS ASSOCIATED WITH IMMUNOCYTE INFILTRATION IN COLORECTAL CANCER
Review round: 2
Reviewer: 1

Output:
Basic reporting: Paper has been much improved- language is clearer, experiments and importance of research very nicely motivated in the introduction. I only have a few minor suggestions.

1. Please provide a citation for line 163, "Tumor infiltrating lymphocytes affect the survival of various cancer patients."

2. Please provide a citation for lines 213-215, "The intestinal ECM...apoptosis."

3. Please provide a brief definition for the TNM cancer staging system prior to its first use.
Experimental design: Very happy with the addition of information about the databases used and methods, as well as the changes to figures, especially regarding the work done for Fig 2.
Validity of the findings: While the decreased expression of CRYAB in COAD tumor tissue compared with normal tissue is consistent with the conclusion that CRYAB could function as a tumor suppressor gene in COAD, the increased expression of CRYAB in highly malignant cancer suggests the opposite. So some explanation or more in depth discussion of how this increased malignancy with increased CRYAB expression fits with the conclusions here would be helpful, even if it's speculation clearly stated as such.
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: CRYAB PREDICTS CLINICAL PROGNOSIS AND IS ASSOCIATED WITH IMMUNOCYTE INFILTRATION IN COLORECTAL CANCER
Review round: 2
Reviewer: 2

Output:
Basic reporting: General
1.	The revised manuscript is improved. The manuscript could still benefit from further grammatical and readability improvements.

Abstract

1.	Line 18 Methods
Please use a more scientific term than “ checked”, for example ‘examined’, ‘investigated’, ‘studied’,’assessed’, ‘quantified’

Introduction

Line 45-54
Is the revised added data about CRC prevalence worldwide or for the U.S.?  Please provide in manuscript.
Experimental design: Methods

1.	Line 106: . Serial sections were generated and select DAB.
Should this sentence be corrected to: Serial sections were collected?
Shouldn’t DAB stain be used after applying the primary and secondary antibodies? Please clarify methodology.

The immunohistochemistry methodology does not match what is written in Figure 2 legend. Please make it consistent.
Validity of the findings: No comment.
Additional comments: No additional comments


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

Input:
Title: A FRESH LOOK AT CLADAROSYMBLEMA NARRIENENSE, A TETRAPODOMORPH FISH (SARCOPTERYGII: MEGALICHTHYIDAE) FROM THE CARBONIFEROUS OF AUSTRALIA, ILLUMINATED VIA X-RAY TOMOGRAPHY
Review round: 1
Reviewer: 1

Output:
Basic reporting: Although the content of this manuscript is generally presented clearly, there are a number of improvements needed:

Starting with the title (and throughout), I don't find the use of the term "tetrapod-like fish" appropriate or helpful. It is not a phylogenetically-precise term (which is  particularly needed in the title). I would suggest use of the term stem tetrapod or finned tetrapodomorph instead. The title might be structured more traditionally with the genus/species followed by "(Megalichthyidae; Tetrapodomorpha).

I think the title also needs to include the entire binomial for the taxon under discussion. I think it future-proofs the publication for a day when additional species of Cladarosymblema are in the literature. This same comments applies throughout the manuscript and I would advocate for use of the species name throughout (and especially in figure captions). The use of C. narrienense is certainly a good option when the genus/species has been used previously in a section.

I find a few places where the language seems too casual or unnecessary. Eg. Line 72 - "handful"; Line 101 - "until now"; Line 115/122 - "is a Quennsland Museum specimen"; Line 212 - "managed to piece together". Perhaps these are personal preferences, but I feel like there are too many "herein" and in the pectoral girdle and fin section the use of "we" is unnecessary.

Numerous figure citations are wrong or incomplete, and generally the citations are unevenly used among the different sections of the manuscript. The authors need to review current citations and add additional citations to better help the readers go from text to figures.

I would comment that there are distinct writing-style differences among different sections of the text. The manuscript would benefit from a more consistent style. I'm not suggesting a re-write, only that one of the authors should review the manuscript with this issue in mind.

Line items:
Line 77 - Megalichthyidae also from Late Devonian (Famennian) of North America (M. mullion from Pennsylvania).
Line 138 - Is dataset storage size relevant?
Line 409 - "step" to "steps"
Line 436 - "Stem-tetrapodomorph" to "Tetrapodomorph"
Line 492 - "represent" to "reveal"
Line 560 - Is "under review" appropriate to cite? (even though authors are on both papers)
Figure 7 - Is the dorsoventral shading necessary? I think it takes away from the scientific clarity. Also, is the color-coding of element names in regions necessary? It creates challenges for readers with different color-perception, and when color printers do not perform properly. For example, I do not see any difference between the skull roof (dark blue) and the opercular series (purple).
Experimental design: The imaging and phylogenetic methods used in the manuscript are state-of-the-art. The manuscript provides new data and appropriate interpretation.
Validity of the findings: The anatomical descriptions are well-supported by the new imaging efforts. The phylogenetic methods and hypothesis are adequately presented.  The methodological details of the phylogenetic analysis are presented but I do not see any indication that the character list and data matrix will be available.
Additional comments: I enjoyed this manuscript and think it is a very useful contribution, although it does need to be edited/revised.


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

Input:
Title: A FRESH LOOK AT CLADAROSYMBLEMA NARRIENENSE, A TETRAPODOMORPH FISH (SARCOPTERYGII: MEGALICHTHYIDAE) FROM THE CARBONIFEROUS OF AUSTRALIA, ILLUMINATED VIA X-RAY TOMOGRAPHY
Review round: 1
Reviewer: 2

Output:
Basic reporting: The study by Clement et al. on the anatomy of the tetrapodomorph fish Cladarosymblema is an important contribution to our knowledge of the diversity and evolution of sarcopterygians.
The text is well written by native English speakers and only a few minor orthographic corrections are needed.
The list of references is extensive and pertinent, although a few additions may be welcome and some errors of citing need to be corrected.
The data are well structured, the figures provide all the necessary information and illustrate well the descriptions in the text, although certain improvements have been suggested (see annotated pdf).
Raw data have been shared and are accessible to interested readers.
Experimental design: The research fits within the aims and scope of PeerJ.
The research questions are well defined, as an exploratory study of the hidden anatomy of previously know and described fossil specimens of an interesting taxon. The three-dimensional preservation of the specimens and the possibilities that virtual microtomography now offers to palaeontologists absolutely justify the use of these techniques in the study of these important fossils.
The methods are correctly described and in detail.
Validity of the findings: The anatomical descriptions use up-to-date terminology and are clearly written, with enough in-depth information.
The conclusions are well stated and reprise the main discoveries of the study.
Additional comments: I have listed a series of comments directly on the pdf file, and I refer the authors to these.

I have, however, certain comments that will need further development by the authors and will be detailed below:

I think further information is needed concerning the status and importance of “osteolepiforms” in the context of sarcopterygian evolution. The term is almost not used in the text and I suspect that it is replaced by “osteolepidids”, which is incorrect. Many readers may be familiar with Eusthenopteron and I consider that a short review of their implications in the study of the fish-tetrapod transition will complement the introduction nicely.

The importance of cosmine in megalichthyids in particular and in tetrapodormorphs in general has not been clearly stated nor explained. The retention of cosmine beyond the Devonian is one of the main features of megalichthyids and may have certainly played a role in the evolution. Many readers may not be familiar with this particular “tissue” and thus a short description and a few extras references may improve the introduction.
I suggest the following ones:
MONDÉJAR-FERNÁNDEZ, J. 2018. On cosmine: its origins, biology and implications for sarcopterygian interrelationships. Cybium, 42, 41–65.
THOMSON K.S., 1975. On the biology of cosmine. Bull. Peabody Mus. Nat. Hist., 40: 1-57.

In general, but especially in the discussion, further information on the paleoenvironment may add more context to the anatomical and evolutionary implications highlighted by the new data. The fact that megalichthyids are primarily freshwater fishes, in contrast with many other early Paleozoic sarcopterygians which are considered as mainly marine fishes, is interesting and should be further developed. Can paleoneurological features be related to ethology or adaptations to certain habitats by megalichthyids? It may be too soon to settle this issue, but some introductory theories may complement the paper and broaden its scope.

Throughout the text and as a piece of general advice, I would initially list the complete name (genus and species) of every taxon, even though in the course of the manuscript only the genus name is used (e.g., Cladarosymblema narrienense first mention, Cladarosymblema after). In case the genus is known by a single species, citing the species every time becomes redundant, but not if there are other species in the same genus.


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 ATLAS OF PHALAENOPSIS EQUESTRIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Orchids are one of the most beautiful and fascinating plant species. The high differences among orchids fascinated a large part of the scientific community during the centuries. Until now, the molecular pathways regarding orchid development are arduous to study for the absence of mutant of this species. The genome and transcriptome sequencing are two pivotal resources to understand which genes are involved in orchid differentiation. The data obtained with this study will be useful to all the scientific community that focus their analysis on orchids to understand which genes are involved in some unknown molecular pathways. The TraVa database will be helpful support for future orchid studies.
I suggest improving the introduction emphasizing the importance of this transcriptome data and why they will be important for the scientific community. It is necessary, in my opinion, to highlight why the transcriptome data is a relevant resource adding some work example where the use of transcriptome data was decisive to understand the role and evolution of some genes in orchid species.
The manuscript is clear and well written. I have listed some correction in the text in the attached file.
The figures are precise. I suggest, if it is possible, to change the interval colour to better highlight the differences of expression among genes, especially in Fig. 2.
Experimental design: No comment
Validity of the findings: I suggest adding to the conclusion the importance of this transcriptome sequencing, the TRaVa database and the orphan genes investigated. I recommend emphasizing on the importance of the data obtained and the use in future of these data.
Additional comments: L.26: Remove “a” between “about” and “half”
L.47: Add “the” before “reliability
L. 79: Substitute “In order to” with “To”
L. 102: Add “an” between “showed” and “extremely”
L. 112: Add “the” before “analysis”
L. 112: Add “the” before “detailed”
L. 129-130: I believe that there is a problem in this part “when transcripts of 21 671 (74%) genes were found in at least one sample.” Probably “when” needs to be changed in “while”. If there isn’t a problem, I suggest changing this phrase because I believe it is unclear.
L. 138-140: “A number of samples where gene is expressed is the simplest method to characterize expression pattern width, as was shown for Nicotiana tabacum (Edwards et al., 2010) or Vigna unguiculata (Yao et al., 2016)” it should be reformulated in “Investigate some samples, where a gene is expressed, is the simplest methods to characterize expression pattern width, as was shown for Nicotiana tabacum (Edwards et al., 2010) or Vigna unguiculata (Yao et al., 2016)”.
L. 142: Replace “less” with “fewer”
L. 146: Add “the” between “on” and “clustering”
L. 147: Replace “less” with “fewer”
L. 155: Add “the” between “in” and “case”
L.156: Add a comma after “count”
L. 162: Replace “oxidation reduction” with “oxidation-reduction”
L. 178: Add “the” before “Graphical”
L. 180: Substitute “number of” with “several”
L. 183: Add “the” between “with” and “undifferentiated”
L. 210: Add commas before and after “however”
L. 214: Remove “an” between “is” and “evidence”
L. 216: Add a comma after “Notably”
L. 226: Remove “the” before “similar”
L. 227: Substitute “In order to” with “To”


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 ATLAS OF PHALAENOPSIS EQUESTRIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: I hope that the author can select several genes to verify whether the selected genes had a tissue-specific expression by qPCR or RT-PCR


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 ATLAS OF PHALAENOPSIS EQUESTRIS
Review round: 1
Reviewer: 3

Output:
Basic reporting: Some references should be added, I mentioned in the "General comments for the author".
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: Line 36: In the genome paper of Apostasia shenzhenica (Zhang et al., 2017)，the author provided the new assembly of Phalaenopsis equestris under original NCBI accession. And this paper should be cited.
Line 90-93: I prefer to move this part to the Introduction. Although transcriptome and genome data were available for P. equestris, transcriptomes provided by author have more samplings and were from a variety named P. equestris var. blue, which helps to enrich the genetic resource for P. equestris. Thus, author should write two or three sentences to illustrate the ornamental value. Also, it will be better to provide the picture of P. equestris var. blue in the supplementary part since the potential utility on the molecular breeding.
Line 117-118: It will be better to change the word rather than "outgroup" since the cluster result is not a rooted tree. Some paper used this expression, but it is easy to make misleading.
Line 119-122: I can’t understand why the expression pattern would be similar for the lack of older tissues? Please illustrate the reason clearer.
Line 125: the same issue about “outgroup”. Use other statement likes “most divergent”or “form the sister cluster…”.
Line 185: "Apostasia shenzhenica", no "schenzhenica". And this paragraph discussed many about MADS box study in orchids, but without any citation.


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 ATLAS OF PHALAENOPSIS EQUESTRIS
Review round: 2
Reviewer: 1

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


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

Input:
Title: TRANSCRIPTOME ATLAS OF PHALAENOPSIS EQUESTRIS
Review round: 2
Reviewer: 2

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


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

Input:
Title: TRANSCRIPTOME ATLAS OF PHALAENOPSIS EQUESTRIS
Review round: 2
Reviewer: 3

Output:
Basic reporting: All pass. I can't judge well about the English expression but I found the sentences can be read easily and didn't make misunderstood. The author cited the related papers as I mentioned in last reviewing.
Experimental design: Pass. The author revised the manuscript according to my comments.
Validity of the findings: Pass. The author revised the manuscript according to my comments.
Additional comments: Pass. The author revised the manuscript according to my 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: ORIGIN OF THE X-CHROMOSOME INFLUENCES THE DEVELOPMENT AND TREATMENT OUTCOMES OF TURNER SYNDROME
Review round: 1
Reviewer: 1

Output:
Basic reporting: Grammar and syntax needs some modifications.
Literature and citations are sufficient
Background could be improved- see Notes to Authors below. Evidence within the discussion (referring to other papers), context, and result reference ranges are lacking.
Figures and tables are easy to read, interpret.
Raw Data not available
Experimental design: Project is within "Aims and Scope" of the journal

The research question is well defined and certainly very meaningful, with great potential to fill a knowledge gap.

Methods should be provided in more detail, expanded - how were assays performed (were estradiol, LH via ICMA, what reference ranges were used and how did this correlate to age, puberty, sex. how were chromosomes of origin detected.

I think the investigation may not be as rigorous as anticipated.

 Standard of ethics appear to have been followed.
Validity of the findings: Concern that the results are not correlated to what is known in this population. Research data/results are provided through Figures and Tables, but it is hard to determine if these data are truly statistically sound without reference ranges or standards provided.

Conclusions are concerning. Some sections of the discussion are inaccurate- see Notes to Authors below.

Conclusions are  not supported by the results obtained in the study. Conclusions are based on extremely limited studies over a very brief timeframe (9 months) that may not best predict outcomes. It is unclear if the authors recognize this limitation, as it is not mentioned anywhere in the manuscript.
Additional comments: This is an interesting study by the authors on clinical effects of parental origin of the retained X chromosome(s) in patients with Turner Syndrome.  The concept of using parent of origin studies is fascinating and there is likely a lot to be learned in this area.  The authors are to be commended for their originality and thoughtful consideration of this project.

Strengths:
sizable number of study participants
thoughtful genetic evaluation for karyotype, parent of origin studies, extensive  laboratory testing
Methods of TS diagnosis, treatment, and dose of therapy are clear

Additional details of this research project are unclear. On line 76, inclusion criteria reads, “suitable for GH” – please define this. It would also add value if you explain how parent of origin studies are conducted.

One concern I have is that the age range of subjects is quite wide. While this is expected, since mildly affected patients have a late diagnosis, and presumably those with late diagnosis also have less potential for growth. Their poorer height outcome may be due to missed treatment, not alternative factors.  In addition, age of subject influences outcomes such as uterine size, growth rates, bone age progression; furthermore, the reference range in different ages is not the same, so cannot be compared.

Importantly, this manuscript does not include standards/reference ranges. For example, definitions for “small uterus” or “large uterus” are missing -  these dimensions vary by age and pubertal status, at minimum. A 12 yo without spontaneous estrogen will be different than a 12 yo with spontaneous, endogenous estrogen. Specifically, this the range of estrogen levels was quite wide- which supports that some patients may have been on estrogen. This can impact the study results in multiple ways.

The authors mentioned a number of laboratory analyses that showed low levels.  The manuscript would be further enriched if the authors explained why those reduced values are (or are not) clinically relevant.  The authors also mention impact of retained maternal X chromosome on prolactin levels. Please provide background on why you are concerned about prolactin levels in patients with TS and how this impacts their management.

Some discussion points are unclear or poorly supported by evidence. Line 167- remove “Besides” and describe how this relationship is changed. Line 168- “GH treatment show restored IGF-1 and IGFBP-3 levels” – but baseline levels in TS are typically normal.

Importantly, the authors should comment if 9 months an adequate time frame to assess growth response in this population?

The manuscript would be greatly enhanced by also providing a section on further work to be done based on these results.  Lastly, consider improvements in grammar, syntax, and English so that this paper appeals to a broad variety of English-speakers.


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: ORIGIN OF THE X-CHROMOSOME INFLUENCES THE DEVELOPMENT AND TREATMENT OUTCOMES OF TURNER SYNDROME
Review round: 1
Reviewer: 2

Output:
Basic reporting: The English language throughout this manuscript could be improved upon by having a colleague who is proficient in English and familiar with the subject matter review your manuscript to insure the most appropriate use of wording and punctuation are addressed.  Some examples where the language could be improved upon include lines 83,112,125,186,187,199,208 and more.

Your background and literature support would be stronger by providing more context of what has been demonstrated regarding height, specifically related to the SHOX gene and epigenetic reports, as well as parent of origin findings related to survivability as well as hypotheses of all survivors are mosaic from previously published literature.
Experimental design: Data regarding cases in which both parents of origin have X chromosome material present in the karyotype could be stronger by substantiating the parent of origin for the presence of the shox gene(s), and which del(X) parental origin material is present.  By grouping the parent of origin and clarifying breakpoints in the tables, such as table 3, it would help the reader more clearly understand the role parent of origin is playing vs. genetic material deleted.
Validity of the findings: The conclusion would be stronger with more details of the substantiated clinical utility of these findings and how this research matters.
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: ORIGIN OF THE X-CHROMOSOME INFLUENCES THE DEVELOPMENT AND TREATMENT OUTCOMES OF TURNER SYNDROME
Review round: 1
Reviewer: 3

Output:
Basic reporting: English language is awkward in many parts, sometimes making difficult to understand the meaning.
Too often you use very long periods! To give you an example, the periods between lines 136 and 140 or between 153 and 156 are excessively long. You must try to use shorter and concise periods, which will certainly be clearer and appreciated by the reader.
Moreover, there are many grammatical errors, even banal (e.g. commas, uppercase or lowercase, etc.).
Another example (line 147): "between two parents"???..Did you maybe mean "among parents"?
Author must submit their manuscript to a native English speaker to bring several important changes and to make their manuscript understandable.
You also didn’t even number the pages of the entire document, which would have facilitated the review process.
Experimental design: Writing of this paper is not the clearest.
Both introduction and discussion should focus on what this study adds to the existing literature.
There are some rough errors, such as the mismatch between the age range expressed at line 75 and line 122.
Another methodological error, in my opinion, is that of line 142: you have taken into consideration, in a fundamentally arbitrary way, only patients between the ages of 5.2 and 10 years. It would have been more appropriate to select sub-groups on the basis of the different growth rates expected in the different age groups.
Also, why did you choose just 9-month GH treatment as duration?
At line 131 it is assumed that patients had a low LH value. You can't make such a statement, as you consider both young and adult subjects, with only the latter with an overt ovarian damage, and therefore with a condition of hypergonadotropic hypogonadism!
At line 135 you claim to have divided patients into three groups, based on the retained X chromosome origin. What is the point, then, of having previously divided patients on the basis of different karyotype groups (Type 1-4)? You should clarify that.
Please add the normative values in Table 2.
Validity of the findings: The subject matter is certainly interesting. ot all conclusions, however, can be drawn with certainty! For example, at line 152, you write: "these results suggest that an elder pregnant woman...". It would be much more appropriate to use a conditional, such as could or may.."these results MAY or COULD suggest that an elder pregnant woman..."
Line 186: From "so far...to effects": Where is the verb in this sentence?
Then you draw conclusions about the link between the mother’s age and the lower prolactin level. Considering that a scientific paper has to be also clinically applicable, what do you find about low levels of prolactin in women? Do you know of any pathology related to hypoprolactinemia?!
In general, the conclusions you draw seem quite "forced", in order to try to add something new to the existing literature on the subject.
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: ORIGIN OF THE X-CHROMOSOME INFLUENCES THE DEVELOPMENT AND TREATMENT OUTCOMES OF TURNER SYNDROME
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: no comment
Validity of the findings: Raw data: Detailed structural karyotype information is not provided, even in the raw data, esp in consideration of breakpoints in genes which may be disrupted.

Pg 15. Discussion regarding maternal age at the time of birth and height increase response should be substantiated further based on literature reports and possible underlying mechanisms to explain the etiology of this finding.

In addition, the maternal origin and paternal origin is not clarified in these cases of maternal age.

Pg 15. "Growth retardation tends to be more sever in patients with XrX,isoXq,and 45,X" yet the findings of this current study contradict these reports as isoXq would have X chromosomes from both parents- when in fact the Xp arm is truly only present from one parent, etc.  It would be a stronger paper to substantiate regions from only one parent vs. chromosome origins from one or both.

Lastly, the conclusion of recommending early childbearing for mothers of children with potential TS is not sensible as most occurrences of TS (esp 45,X) are sporadic and not inherited.
Additional comments: no comment


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

Input:
Title: THE PHYLOGENETIC NOMENCLATURE OF ORNITHISCHIAN DINOSAURS
Review round: 1
Reviewer: 1

Output:
Basic reporting: This style of paper (i.e., the revision of nomenclature to fit the requirements of the new PhyloCode) has already shown up for other taxa and is an expectation for our new taxonomic system. This is just a personal thought and not a critique of the paper or such, but I do feel mildly troubled that the coiners of the original terms are not invited on such papers. Obviously when Marsh and Seeley and Nopsca are not around to participate I have no qualms about this, but when those who have actually created these names in the context of the phylogenetic system of nomenclature are still extant, I find it a tiny bit disconcerting they aren’t in on these revisions. Of course, this would result in extremely long authorship (perhaps even as long a list  as on a typical modern genome or physics paper), and would be unwieldy both in organizing the manuscript and in citing the new name. Still, it just strikes me as a bit odd. That said, I salute the authors here for taking up the task, and they have done an excellent job in doing so.

I have little to comment on in terms of the body of the paper: the definitions and anchor taxon choices seem very reasonable, and the authors show every evidence of respecting the original spirit of the terminology (e.g., the distinction between a Norman-esque Hypsilophodontia and a more standard Hypsilophodontidae.) Some specific cases are discussed below in “General Comments.”
Experimental design: The paper is nomenclatural, not experimental. No hypotheses were tested as such.

That said, I very much appreciate Figure 2 and the demonstration of how the system operates under two mutually exclusive topologies. However, these are only slightly different situations from each other, and I believe I would be extremely illustrative to show how the nomenclature operates under some radically different topologies. In particular, I think using Yang et al. 2020 (reference below: this paper restores a rather refreshingly old-fashioned pre-2010s broadly inclusive Ornithopoda), Madzia et al. 2018 (with its ultra-reduced Ornithopoda), and Dieudonné et al. 2020 (“everything you know about neornithischians is wrong; heterodontosaurs are basal pachychephalosaurs”) could be very instructive to how the nomenclature works under alternative hypotheses.

Yang, Y., W. Wu, P.-E. Dieudonné & P. Godefroit. 2020. A new basal ornithopod dinosaur from the Lower Cretaceous of China. PeerJ 8: e9832. Doi: 10.7717/peerJ.9832
Validity of the findings: Again, this paper is nomenclatural, so it doesn't have "findings" as such.
Additional comments: COMMENTS
Line 410		Lucas (in early editions of his textbook Dinosaurs: The Textbook) used “Pachyrhinosaurinae” instead of “Centrosaurinae”, during the interval when it was thought that “Centrosaurus” was an invalid junior homonym of “Kentrosaurus”. However, the only case I can find where Pachyrhinosaurinae was used in a technical paper was in a comment by Lucas et al. (2016, p. 202) where they claim that this should be the name to use, but employ Centrosaurinae instead.

Lucas, S.G., R.M. Sullivan, A.J. Lichtig, S.G. Dalman & S.E. Jasinksi. 2016. Late Cretaceous dinosaur biogeography and endemism in the Western Interior Basin, North America: A critical re-evaluation. New Mexico Museum of Natural History and Science Bulletin 71: 195-213.
https://www.researchgate.net/profile/Asher-Lichtig-2/publication/303936024_Late_Cretaceous_dinosaur_biogeography_and_endemism_in_the_Western_Interior_basin_North_America_A_critical_re-evaluation/links/575ef2b708aec91374b42caa/Late-Cretaceous-dinosaur-biogeography-and-endemism-in-the-Western-Interior-basin-North-America-A-critical-re-evaluation.pdf

line 565 ff	A rare case when I disagree with the authors definitional decision. While it is true that Norman clearly conceived of Clypeodonta as a clade within Ornithopoda, a Hypsilophodon+Iguanodon clade will always exist in any phylogeny and seems worthy as a named entity even in cases where it contains Cerapoda rather than being contained within it. (Such cases exist on the saurischian-side of things: bird phylogenetics can never settle if Ornithurae (the Hesperornis+Aves clade) contains Carinatae (the Ichthyornis+Aves clade) or is instead contained by it.) Thus, I would think they could remove the ∈ Ornithopoda specifier so that the name might serve in contexts such as Madzia et al. 2018.

Line 718	Euceratopsia has been missing from my life and I wasn’t even aware of that fact; thank you for this very useful clade name!

Line 1601	There is no necessity for this suggested inclusion, but given that a masterpiece of Parasaurolophini-literature has just been published (Ramírez-Velasco et al. in press), it might be useful to have this listed among the reference phylogenies:
Ramírez-Velasco, A.A., F.J. Aguilar, R. Hernández-Rivera, J.L.G. Maussán, M.L. Rodríguez & J. Alvarado-Ortega. In press. Tlatolophus galorum, gen. et sp. nov., a parasaurolophini dinosaur from the upper Campanian of the Cerro del Peublo Formation, Coahuila, northern Mexico. Cretaceous Research in press. Doi: 10.1016/j.cretres.2021.104884

Lines 1650-1652	Wise move on “Polacanthidae”.

Line 1906 ff	In Dieudonné et al. 2020 and Yang et al. 2020 Thescelosaurus spp. are on a branch by themselves, exclusive of Orodomeus, Hypsilophodon, or Parksosaurus. In those two phylogenies that clade is simply “Thescelosaurus” but one can envision that additionally Jurassic and pre-Maastrichtian taxa closer to Thescelosaurus than to all other currently known dinosaurs (required by these topologies) will be discovered. Do you really want to deprive them of being in “Thescelosauridae” simply because Orodromeus is not with them? Do you really want that on your conscience? (In other words, I wonder if a definition that doesn’t necessarily include Orodromeus might work? At least consider this.)
	For what it is worth, I am all for the definition of Thescelosaurinae provided.

Line 1975	Please correct the typo here: “Thyrophora”.

Line 2047	I wonder, relative to all this business at the base of Ornithischia, if it might not be prudent to include a clade name for Pisanosaurus + Genasauria, provided that Pisanosaurus is closer to Genasauria than to Silesaurus, Sauropodomorpha, or Theropoda. Marsh’s 1894 Predentata might serve.
Marsh, O.C. 1894. The typical Ornithopoda of the American Jurassic. American Journal of Science, Series 3 48: 85-90.

Line 2059	Actually, Dieudonné et al.’s 2020 phylogeny reduces the total “gappiness” of the ornithischian record. The addition of extensions of Ornithopoda from the Middle to Early Jurassic and of Ceratopsia from the earliest Late to Early Jurassic is a smaller amount of time than the earliest Oxfordian-to-Turonian gap in Pachycephlosauria required in the standard topology.

Line 2104 ff	A very important point about “Ankylosauromorpha”.

Line 2138	In this discussion, Yang et al. 2020 should be added (and in particular as it has the most inclusive recent incarnation of Ornithopoda).

Line 2169	In a similar context, Ramírez-Velasco et al. in press might be added to this discussion of hadrosaurid ingroup relationships.


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 PHYLOGENETIC NOMENCLATURE OF ORNITHISCHIAN DINOSAURS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The MS by Madzia et all provides a timely set of phylogenetic definitions for ornithischian clades, following the publication of the PhyloCode and Phylonyms. My understanding is that most of the definitions are adequate, balancing the historical understanding and current use of the names. My main concerns about some of the definitions are highlighted below and, along with other minor (typos and style) suggestions, in the annotated PDF.

Many of the “primary reference phylogenies” do not have all the specifiers figured in the tree. Even if this is obvious in most of the cases (e.g., Ankylosaurus magniventris is within Ankylosauria in Fig. 12 of Maidment et al. 2020), in other cases this imprecision may render the definition not promptly understandable, especially for the non-specialist. I strongly recommend that, for every specifier not strictly included in the “primary reference phylogeny”, its position should be indicated in the  tree as, e.g., “Ankylosaurus magniventris is nested within Ankylosauria in Fig. 12 of Maidment et al. (2020)”. Alternatively, another “primary reference phylogeny” may be chosen.
Below is an exhaustive list of such cases, but please make sure I did not miss any of them …
For Ankylosauria, Stegosaurus stenops is not indicated in Fig. 11 of Arbour and Currie (2016).
For Ankylosauridae, Nodosaurus textilis is not indicated in Fig. 11 of Arbour and Currie (2016).
For Cerapoda, Triceratops horridus and Pachycephalosaurus wyomingensis are not indicated in Fig. 4 of Madzia et al. (2018).
For Ceratopsia, Ceratops montanus and Pachycephalosaurus wyomingensis are not indicated in Fig. 10 of Morschhauser et al. (2019).
For Euiguanodontia, Dryosaurus altus and Camptosaurus dispar are not indicated in Fig. 13 of Coria and Salgado (1996).
For Eurypoda, Stegosaurus stenops is not indicated in Fig. 3 of Thompson et al. (2012).
For Genasauria, Triceratops horridus and Ankylosaurus magniventris are not indicated in Fig. 16 of Han et al. (2018).
For Heterodontosauridae, Triceratops horridus, Stegosaurus stenops, and Pachycephalosaurus wyomingensis are not indicated in Fig. 4 of Madzia et al. (2018).
For Hypsilophodontia, Tenontosaurus tilletti is not indicated in Fig. 50 of Norman (2015).
For Jeholosauridae, Triceratops horridus and Pachycephalosaurus wyomingensis are not indicated in Fig. 25 of Herne et al. (2019).
For Marginocephalia, Ceratops montanus, Triceratops horridus and Pachycephalosaurus wyomingensis are not indicated in Fig. 16 of Han et al. (2018).
For Neornithischia, Triceratops horridus, Ankylosaurus magniventris and Stegosaurus stenops are not indicated in Fig. 4 of Madzia et al. (2018).
For Ornithopoda, Triceratops horridus and Pachycephalosaurus wyomingensis are not indicated in Fig. 4 of Madzia et al. (2018).
For Pachycephalosauria, Triceratops horridus and Ceratops montanus are not indicated in Fig. 27 of Schott and Evans (2017).
For Pachycephalosauridae, Heterodontosaurus tucki is not indicated in Fig. 27 of Schott and Evans (2017).
For Stegosauria, Ankylosaurus magniventris is not indicated in Fig. 12 of Maidment et al. (2020).
For Thyreophora, Triceratops horridus and Ankylosaurus magniventris are not indicated in Fig. 16 of Han et al. (2018).

The composition of some of the defined clades is in fact uncertain based on some of the “primary reference phylogenies”, because the pointed nodes are represented by polytomies. In such cases, it would be adequate to either change the “primary reference phylogenies” or discuss the taxa that may alternatively belong or not into the named clade.
Below is an exhaustive list of such cases, but please make sure I did not miss any of them …
For Elasmaria, it is not clear in Fig. 31 of Rozadilla et al. (2019) if Anabisetia saldiviai, Atlascopcosaurus loadsi, Fulgurotherium austral, Gasparinisaura cincosaltensis, Kangnasaurus coetzeei, Morrosaurus antarcticus, Notohypsilophodon comodorensis, Quantassaurus intrepidus and Trinisaura santamartaensis belong into the clade.
For Genasauria, it is not clear in Fig. 16 of Han et al. (2018) if Lesothosaurus diagnosticus belongs into the clade.
For Hadrosauridae, it is not clear in Fig. 18 of Prieto-Márquez et al. (2020) if Eotrachodon orientalis belongs into the clade.
For Hadrosauriformes, it is not clear in Fig. 12 of Madzia et al. (2020) if Siamodon ninmgami, Hypselospinus fittoni, Barilium dawsoni and Lurdusaurus arenatus belong into the clade.
For Hadrosauroidea, it is not clear in Fig. 12 of Madzia et al. (2020) if Siamodon ninmgami, Hypselospinus fittoni, Barilium dawsoni and Lurdusaurus arenatus belong into the clade.
For Hadrosauromorpha, it is not clear in Fig. 12 of Madzia et al. (2020) if Zouyunlong huangi and Sirindhorna khoratensis belong into the clade.
For Heterodontosauridae, it is not clear in Fig. 4 of Madzia et al. (2018) if Pisanosaurus mertii belongs into the clade.
For Iguanodontidae, it is not clear in Fig. 12 of Madzia et al. (2020) if Siamodon ninmgami, Hypselospinus fittoni, Barilium dawsoni and Lurdusaurus arenatus belong into the clade.
Experimental design: No comment.
Validity of the findings: See basic reporting
Additional comments: No comment


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

Input:
Title: THE PHYLOGENETIC NOMENCLATURE OF ORNITHISCHIAN DINOSAURS
Review round: 1
Reviewer: 3

Output:
Basic reporting: This contribution is clearly written and the standard of written English is excellent throughout. It is extensively referenced though it might be useful to add a brief overview of changes and conflicts in ornithischian classification through time in the Introduction to set the scene for some of the subsequent discussion, although I wouldn't regard this as mandatory (and some of this information is mentioned at specific points in the MS where most directly relevant). There are no raw data to share as this is essentially a meta-analysis, pulling together published information in a novel way. Similarly, there is no hypothesis-testing here: the authors are instead providing a framework for future work, so the MS is fully self-contained in this respect. The paper is well referenced though there are a few minor issues that need to be addressed (missing references, a couple of superfluous references, one or two incorrect taxonomic references; these are noted on the annotated .pdf).
Experimental design: The paper is written in the context of the recently published PhyloCode and offers a novel perspective on the phylogenetic definition of ornithischian dinosaur clades, building upon previous work in the area. They follow the articles of the PhyloCode and use topologies taken from a range of published phylogenetic analyses to formalize and update a large number of clade definitions. The authors have clearly gone to some lengths to provide rigorous definitions and have attempted to future-proof some of these against possible future changes in tree topology, reflecting current uncertainties.
Validity of the findings: I read this paper through the lens of someone who is unconvinced of the need for the PhyloCode and who sees a number of disadvantages in this approach. That said, I cannot fault the authors' approach to the topic, which is internally consistent and fills a gap left in the current PhyloCode compendium, which omits ornithischian dinosaurs. The taxonomic work underpinning this article is solid and most of the things I find unpalatable about this article relate to the rules of PhyloCode itself, rather than the authors' conclusions or approach. As it stands, the MS is essentially a catalogue of definitions, with some commentary on several current problems in ornithischian phylogeny, which is entirely appropriate. I make a number of minor suggestions on the attached .pdf, but would note the following suggestions that the authors might like to consider in terms of a more general commentary on the application of PhyloCode through the example of ornithischians:
1. One of the aims of taxonomy is stability, and given that many parts of the ornithischian tree are currently highly labile I think setting these definitions in stone may be too soon (the lack of consensus over some major nodes in the tree means that there are at least three competing broad phylogenies available, as well as more minor re-arrangements within more deeply nested clades). The authors do discuss this, and have clearly thought about these issues, but I wonder if they could make more discussion of these potential conflicts to show how definitions (or names at least) for some taxa could change with changes in tree topology. Adding a figure to show an example or two of these changes could be useful for readers.
2. The PhyloCode has some areas that conflict with ICZN rules (e.g. over authorship of family-group names and the Principle of Coordination). This means that we can expect some conflicts when comparing this new scheme to the older literature. Also, as the ICZN isn't going anywhere, and as there's no compulsion for any individual researcher or journal to adopt PhyloCode (whereas ICZN rules are currently embedded in many journal policies), we could be in for a messy time taxonomically. For example, it would be entirely possible for different groups of researchers to name or resurrect a taxon under ICZN rules that would have different authorship under PhyloCode rules. This doesn't seem like a recipe for taxonomic stability.
3. It would be useful to know how the authors selected their reference phylogenies, as there's an ever increasing field to choose from. Are there consistent standards or is the choice subjective? At the moment, the authors provide no obvious rationale for choosing one reference phylogeny over another. Are the authors selecting them on the basis of taxonomic scope, numbers of characters, a particular type of analysis (e.g. MP vs ML), a particular type of standard tree topology (e.g. strict consensus) or some other criterion? As these trees are forming the backbone for a rigid set of definitions, which are meant to be in place for sometime, it would be good to know what the criteria for these choices are.
4. It seems bizarre to me that PhyloCode allows clade specifiers that are taxonomically indeterminate at the genus and species level, just because their name (historically) was the basis for a taxon name etymologically. Taxonomies should be based on clearly definable entities not ones that are essentially acting as wildcards within a tree (especially within a set of rules that is meant to be based explicitly on tree-based thinking).
Additional comments: A few minor comments:
1. I think your definition of 'formal' is equal to pre-PhyloCode. Most of us would probably consider any published definition as 'formal', especially those that did mention what type of clade definition and how it was specified. You might consider tweaking this a little as it slightly belittles the work of others who spent considerable time thinking about these issues before the publication of PhyloCode.
2. You could consider adding something on how any of your definitions of very early nodes might change if the enigmatic dinosaur Chilesaurus is an early member of Ornithischia, as suggested by a couple of papers (Baron & Barrett, 2018; Müller & Dias-da-Silva, 2019; Dieudonné et al., 2020).
3. A couple of taxon authorships are incorrect (Polacanthus, Dryosauridae; see .pdf).
4. One or two suggested minor tweaks to clade discussions (Iguanodontoidea, Ankylosauromorpha; see .pdf).
5. Minor referencing issues mentioned in .pdf.


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 PHYLOGENETIC NOMENCLATURE OF ORNITHISCHIAN DINOSAURS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The manuscript is clearly written, and is extensively referenced (indeed, the few mis-referenced taxon names in the first version are now corrected.)

The flow of the paper works well.

This will be an important reference for future workers.
Experimental design: Not an experimental paper as such, so n/a.
Validity of the findings: Again, this paper doesn't have "findings" as such.
Additional comments: The previous manuscript was already in quite a fine shape, and post-review it is even more improved.

I look forward to its 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: OVEREXPRESSION OF FUCOSYLTRANSFERASE 8 REVERSES THE INHIBITORY EFFECT OF HIGH-DOSE DEXAMETHASONE ON OSTEOGENIC RESPONSE OF MC3T3-E1 PREOSTEOBLASTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript is well written with clear and professional English. The basic knowledge is provided with sufficient details to readers in the introduction to understand the background of this study. The figures are high-resolution and clear. Raw data are provided.
Experimental design: Long-term use of dexamethasone leads to osteoporosis by inhibiting TGF-b. FUT8 is an essential enzyme for the stimulation of TGF-b/smad pathway. This study demonstrated the involvement of TFG-b in osteoporosis induced by high concentration of dexamethasone, potentially by downregulation of FUT8. By overexpressing FUT8 in cells, the authors show that the inhibitory effect of high-dose dexamethasone is reversed, confirmed by the TGF-b binding efficiency and the levels of fucosylation. The hypothesis was well defined. The experiments were well designed with sufficient technical and biological repeats.
Validity of the findings: The data are solid and well interpreted with valid statistics.
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: OVEREXPRESSION OF FUCOSYLTRANSFERASE 8 REVERSES THE INHIBITORY EFFECT OF HIGH-DOSE DEXAMETHASONE ON OSTEOGENIC RESPONSE OF MC3T3-E1 PREOSTEOBLASTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: High-dose and long-term of glucocorticoid  treatment may lead to osteoporosis and osteonecrosis. Thus, the identification of key molecules involved in glucocorticoid-induced osteoporosis is important for improving bone regeneration in glucocorticoid therapies. The study showed that overexpression of FUT8 facilitates osteogenesisin dexamethasone therapies by counteracting the inhibitory effect of dexamethasone on TGF-β signaling. The study is interesting, but some concerns need to be addressed.
1. The Figure 1 should be omitted, and the schematic diagram based on research results is supplemented.   2. It is better if the authors check the primary osteoblasts isolated from in vivo experiments.
3. The Figure 2,3, why was the Quantitative real-time PCR measured only at day 3 and not more time points?


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: OVEREXPRESSION OF FUCOSYLTRANSFERASE 8 REVERSES THE INHIBITORY EFFECT OF HIGH-DOSE DEXAMETHASONE ON OSTEOGENIC RESPONSE OF MC3T3-E1 PREOSTEOBLASTS
Review round: 1
Reviewer: 3

Output:
Basic reporting: In general, the study related to the potential “Overexpression of fucosyltransferase 8 reverses the inhibitory effect of high-dose dexamethasone on osteogenic response of MC3T3-E1 preosteoblasts” is very interesting. The research data submitted is also very sufficient which is accessed by several appropriate approaches. These findings will pave the way for therapeutic strategies to improve bone regeneration in glucocorticoid therapy through activating TGF-β at its receptors.
Some points to note are:
1. What should be criticized is that TGF- β activation at the TGF b superfamily receptor has also been reported to inhibit the differentiation stage from immature osteoblasts to osteoblasts, also inhibits RANKL/OPG which has an impact on decreasing bone mineralization as reported by Wu et al (2016). ) TGF-β and BMP signaling in osteoblast, skeletal development, and bone formation, homeostasis and disease, Bone Research 4(1):16009, DOI 10.1038/boneres.2016.9 (lines525-527). Will the overexpression of fucosyltransferase-8 improve and accelerate bone mineralization? In this research report there is no direct evidence for this purpose.
2. The methods in abstract lines 34-36 require a brief purpose of using the method so as to provide an illustration of the approach used. Not just a listing of the methods during the research. Also at the conclusion of line 50 …osteogenesis in dexamethasone therapies by….. does not match the reported study results.
3. In the introduction, it is written very well and clearly
Experimental design: The methods written in the manuscript has been carried out in detail, clearly and is easy to follow.
Validity of the findings: I have carefully studied the reported data. Data were obtained by standard design with adequate replication. There needs to be a quality improvement on some of the figures.
1. The results of the study, Figure 1 should be discarded because it is only a prediction that will obscure the results of this well-done research. The schematic image is also very unclear regarding the black arrow and the presence of fucosyltransferase 8 either intracellular or extracellular site.
2. Figure 4 panel D should be completed with pEGFP and pEGFP-Fut8 data bands.
3. Figure 5 panel A requires high resolution so that the overlay between DAPI and LCA staining can be seen clearly. Also on panels B and C must be completed with pEGFP and pEGFP-Fut8 data bands.
Additional comments: There are 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: OVEREXPRESSION OF FUCOSYLTRANSFERASE 8 REVERSES THE INHIBITORY EFFECT OF HIGH-DOSE DEXAMETHASONE ON OSTEOGENIC RESPONSE OF MC3T3-E1 PREOSTEOBLASTS
Review round: 2
Reviewer: 1

Output:
Basic reporting: OK
Experimental design: OK
Validity of the findings: OK
Additional comments: NO


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: OVEREXPRESSION OF FUCOSYLTRANSFERASE 8 REVERSES THE INHIBITORY EFFECT OF HIGH-DOSE DEXAMETHASONE ON OSTEOGENIC RESPONSE OF MC3T3-E1 PREOSTEOBLASTS
Review round: 2
Reviewer: 2

Output:
Basic reporting: After thoroughly reviewing the revised version of the manuscript, I think that there has been a very significant improvement. All answers to questions and clarification of critical points have been well addressed by the author(s). Unnecessary schematic drawings have been removed. Likewise, images that need to be increased in resolution have also been done well. I take up a full explanation related to the completeness of the data to be part of things that need to be clarified. Therefore, I can accept all points that have been finalized and revised in the last version of this manuscript.
Experimental design: The experimental design is apparent and easy to understand
Validity of the findings: The data is very sufficient
Additional comments: No 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: PROGNOSTIC VALUES OF THE CORE COMPONENTS OF THE MAMMALIAN CIRCADIAN CLOCK IN PROSTATE CANCER
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors evaluated the potential role of the core components of the mammalian circadian clock (CCMCCs) in prognosis prediction in patients with prostate cancer (PC). They found the circadian clock-based risk score model can be useful for prognostic prediction. This is an interesting study for further investigations of the circadian clock‐related molecular mechanisms and the development of therapies for cancer. However, a roubst limitation of this study decreased the importance of the results. The reviewer would like to suggest several key points to improve this manuscript.
Experimental design: #1 The authors need to show the background of patients. It is difficult to find clinical utility from the limited information of the baseline characteristics of patients. The reviewer speculates this study included patients with localized disease alone. But patients with N1 had different treatment strategies and outcomes. The authors need to recognize that the outcome analysis needs a specific population based on the standard of care (such as surgery/radiotherapy for localized disease, systemic androgen deprivation therapy for advanced (N1) disease). The reviewer speculates the clinical implication might be different between the T2N0 disease and T3-4/N1 disease.

#2 The authors need to compare the clinical utility of the circadian clock-based risk score model in combination with robust clinical prognostic factors (Gleason score, T stage, N stage, and PSA,  a high-risk localized disease [NCCN or D'Amico criteria]).  Again, the key limitation of this study is the mixed population in disease stage and treatment. As it is not demonstrated in the current manuscript, the reviewer could not judge the clinical implication of these scores. The authors need to address this point clearly. Who will have benefit from this circadian clock-based risk score model?

#3 The authors showed many analyses for outcomes. It is confusing. Also, multiplicity issues have arisen in statistical approaches. The authors need to reconstruct the outcomes for the main purpose (ex. 9 of key genes and circadian clock-based risk score model in disease-free survival).

#4  Although the clinical implication of disease-free survival in the localized disease is important, the authors need to show the utility of this model for overall survival or metastasis-free survival, which is the key endpoint of prostate cancer study.

#5 How many patients are included in the survival analysis? The authors need to show the numbers of patients in the figures.
Validity of the findings: It is important that the understanding the role of the circadian clock in PC, but this study could not the rationale of the role of CCMCCs in PC. Many readers would like to know WHY? Although the authors discussed some points in the discussion, the authors had better address the link of other key prognostic genes (such as PTEN, TP53, BRCA, ATM, etc). Otherwise, the clinical implication of the circadian clock-based risk score model for prognostic prediction is weak.
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: PROGNOSTIC VALUES OF THE CORE COMPONENTS OF THE MAMMALIAN CIRCADIAN CLOCK IN PROSTATE CANCER
Review round: 1
Reviewer: 2

Output:
Basic reporting: It is an interesting study with novel findings. The authors tried to identify the roles of CCMCCs in prognosis prediction of prostate cancer. Since the molecular pathogenesis of PCa is still poorly known, the identification of novel oncogenes might provide novel possible targets for therapeutics. However, several points of concern, below described, would require further attention from authors and should be addressed before further consideration.
Experimental design: In clinical association part, some other aspects, such as Gleason score, PSA, should be evaluated.
Validity of the findings: Maybe the authors need to confirm the results of some vital CCMCCs in PCa using in vitro or in vivo experiments.
Additional comments: 1. The author could introduce some details of PCa in the introduction section.
2. This manuscript focused on the roles of critial clock-related genes in prostate cancer prognosis, the title should be re-written and made clearer.
3. The authors should define the CCMCCs in details in the intoduction section.
4. In discussion section, the authors could provide some discussion on the clinical significance of this study.
5. Several typos have been identified and they should be revised. It might benefit a round of English revision.


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: PROGNOSTIC VALUES OF THE CORE COMPONENTS OF THE MAMMALIAN CIRCADIAN CLOCK IN PROSTATE CANCER
Review round: 2
Reviewer: 1

Output:
Basic reporting: It is an interesting study with novel findings. The authors tried to identify the roles of CCMCCs in prognosis prediction of prostate cancer. Since the molecular pathogenesis of PCa is still poorly known, the identification of novel oncogenes might provide novel possible targets for therapeutics.The authors satisfactorily addressed most of the issues raised by the reviewers.
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: DISTRIBUTIONS OF EXTINCTION TIMES FROM FOSSIL AGES AND TREE TOPOLOGIES: THE EXAMPLE OF MID-PERMIAN SYNAPSID EXTINCTIONS
Review round: 1
Reviewer: 1

Output:
Basic reporting: On the whole I think the paper is excellently written, with a clear background provided and figures and data all clear. The paper is by necessity very equation-heavy, but I think they do a fine job of supplementing this detail with an explaination of exactly what is being output by the analysis. There are a couple of points where I think things need to be clarified, and a couple of statements that I think are unsupported (see general comments below), but on the whole the basic reporting is excellent
Experimental design: On the whole the method seems sound. The R package is uploaded in github with instructions on how to run through the analyses. However I would suggest that an R script, raw data and isntructions also be uploaded as a supplement, purely for purposes of repeatability; the actual analysis run in this paper should be set in stone, and github be used to track updates and advances on the method.

I do have some issues with the simulation study and also the phylogenetic framework used in the study (see general comments below) but these should be fairly easy to resolve.
Validity of the findings: As I stated above, I do have some issues with the simulation study and the phylogenetic framework employed, but these shouldn't be too horrendous to resolve.
Additional comments: This paper represents a useful contribution to the array of methods for studying extinction in the fossil record. The authors have put a lot of thought into the study design, and also present a useful empirical example with implications for early tetrapod evolution.

On the whole I strongly recommend this paper be published, and I think it will represent a useful framework for future macroevolutionary analyses. I do have a few suggestions for both the empirical and simulation studies, and also think there are some points where statements need further support or clarification before publication.

For the empirical studies, I think the phylogenetic framework used could do with a few updates. I know the tree figured is an illustrative one drawn from several analyzed, but some of = the relationships shown are contradicted by recent updates to pelycosaur phylogeny and should not have been included in analysed trees. Ones that leapt out at me are: that Milosaurus is likely not an ophiacodontid (Brocklehurst & Frobisch 2018, Journal of vertebrate Paleontology volume 38); some rejigging required to the sphenacodontid phylogeny based on the most recent assessment (Brocklehurst & Brink 2017), including that Sphenacodon, Ctenorhachis and Ctenospondylus form a clade; not sure why Echinerpeton has been allowed to form a closer relationship with Varanosaurus than with Ophiacodon, when in all analyses that have included it it has formed an outgroup to a clade containing Varanosaurus and Ophiacodon (see updates to the Benson analysis, in particular from Mann & Patterson 2020, Journal of Systematic Paleontology volume 17).

Another idea that the authors may like to try (but I'd consider this not compulsory) is, instead of drawing equally parsimonious trees for analysis, and then choosing one at random for illustration, would be to resolve polytomies via analysis with the fossilised birth death model, constraining the tree in the same way as has been done before, and running an FBD analysis using observed tip age estimates, would resolve the polytomies based on the age priors and other FBD parameters. The analyses could be carried out on randomly drawn trees from the posterior and the maximum clade credibility tree could form the basis of the figures

For the simulation studies, the authors demonstrate that their method outperforms the Strauss & Sadler method, the oldest method of the family they examine. But I do wonder why they limit their comparison to just that method. After all there have been a whole host of expansions on that theme, as well as some methods that have used the concept but taken a new approach. I am particularly thinking of the  Creeping-Shadow-of-a-doubt method (Alroy 2014, Paleobiology volume 40) and GRIWM (Bradshaw et al 2012, Quaternary Science reviews volume 33); although the former has not been widely used, the latter has been rather popular particularly in studies of the Pleistocene extinction. I think it would be useful to see how your method compares to other advances that have been made since 1989.

Some more specific line by line comments:

Line 56-60: “A third problem of the classical taxic approach is that the known stratigraphic range of taxa typically underestimates their true stratigraphic range (real age of appearance and extinction), a problem that is likely to be especially acute for taxa with a poor fossil record (Strauss and Sadler, 1989). Most recent analyses using the taxic approach still rely on a fairly literal reading of the fossil record to the extent that they use first and last stratigraphic occurrence data as if it were the true stratigraphic range of taxa.”
- I'm not sure the authors are being entirely fair here, particularly as some of the studies cited as using the classic taxonomic approach on lines 41-42 employ sampling corrected estimates of extinction (e.g. Brocklehurst 2018 uses the second for third correction). Such methods don’t endeavor to extend the ranges of specific taxa, it is true, but they definitely don’t make the assumption that the observed origination and extinction of a taxon is true, rather they seek to correct for the gappiness of the fossil record by adjusting the estimates up or down depending on how incomplete the fossil record of that time is. I would frame the issue as your method places confidence intervals on the extinction extimate for specific taxa, not that other studies of extinction have assumed that the observed extinction time is true (if you read most of the papers you cite on lines 41 and 42, it is clear most of them absolutly do not assume this; they just account for it as a general sampling issue rather than endevouring to resolve it for each specific taxon).

Line 156: “A recent literature review of Middle Permian amniote-bearing localities (Olroyd and Sidor, 2017) shows that the assumption of a reasonably homogeneous fossilization rate (worldwide) through the studied time interval (Bashkirian-Roadian) is reasonable”
This is an absolutely bizarre statement that I really cannot support. First, I have had a quick look at the paper cited and I can't find anywhere a suggestion anything like that! Even if there is something I’m missing, can you really take a statement like that from a review of the Middle Permian, and assume it applies from the Pennsylvanian through to the earliest middle Permian? I really doubt it. The Carboniferous and early Permian consist of preservation modes ranging from Texas red bed formations to preservation within fossilised tree truks to cave deposits. To assume that fossilisation potential and rate is homogenous across these preservation modes flies in the face of common sense, as well as actual study of preservation (e.g. Texas red beds selectively preserve larger taxa [Behrensmeyer 1988, Palaeogeography, Palaeoclimatology, Palaeoecology volume 63] while Richards spur has a mode of preservation better suited to smaller taxa [MacDougal et al. 2017, Palaeogeography, Palaeoclimatology, Palaeoecology volume 475]). I don’t think the variation in fossilisation rate is a fatal flaw that will invalidate the study; after all it applies to most methods. Why not just acknowledge that it’s a widely applicable bias that is not accounted for, rather than endeavor to justify it in this rather spurious way?

Line 369-370: “The computation presented above allows us to determine the distribution of the extinction time of a subset of taxa in the case where where the tree topology.” The wording is ambiguous as to whether "distribution" meant a range of exact extinction estimates of each taxon in the subset, or a probability distribution of extinction estimates. I assume the latter so maybe specify a probability distribution. Also note the word “where” has been repeated

Line 511: "The finding that one of three clades studied here (Sphenacodontidae) has a fairly high probability of having become extinct in the Guadalupian may seem surprising at first sight, given the lack of records after the Kungurian."
- In their discussion of this surprising result,  no specific mention is made (just rather vague hints) that the fossil record from North America and Europe, where Sphenacodontidae were found, is not present beyond their last appearance. So if the confidence intervals suggest they survived beyond their last appearance, that seems the most likely explanation.
- This point did draw another to my attention: from their discussion and the figures I infer that the authors are using ages of the formations consistent with those advocated by Lucas, rather than the Roadian age for the Chickasha and San Angelo formation advocated by eg Reisz & Laurin 2001, Benton 2012 Geology volume 40, Brocklehurst 2020 Proceedings of the Royal Society B volume 287. Maybe good to state this explicitly, as this does impact on your discussion regarding competition between therapsids and pelycosaurs e.g. line 546: "The dynamics of biodiversity changes in synapsids similarly shows that therapsids surpassed geologically older synapsid clades in biodiversity sometime in the Roadian (Brocklehurst et al., 2013, fig. 1)." the study cited uses the Roadian age for these formations, so there was an observed interval of temporal overlap between the therapsid-bearing formations of Russia and the pelycosaurs-bearing formations of North America.

Line 503: "compatible with (without proving) a mild, diffuse crisis spanning much of the Artinskian and Kungurian, as suggested by Benton (1985, 1989) and by Brocklehurst et al. (2013)." Don't think Brocklehurst et al. 2013 should be cited here. Its been a while, but I'm fairly sure I never suggested even a mild crisis spanning the Artinskian and Kungurian; rather I suggested the Artinskian was an interval of recovery from a mild crisis at the end of the Sakmarian, and the crisis was concentrated in the late Kungurian (also what I suggested in Brocklehurst 2018, cited in your work).

Figure 3: I know you acknowledge that the node ages of the phylogeny are not accurate, and I know the node ages are not relevant for the inferences of extinction. A phylogeny with accurate node ages is shown in another figure. All of which makes me wonder what the point of this figure is? Why not put the information shown (the probability distribution of the extinction estimates) on a figure with accurate node ages? This figure will just cause confusion.

With these changes made, I think this study will represent an excellent contribution

Neil Brocklehurst