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: ENDOCRANIAL ANATOMY OF THE CERATOPSID DINOSAUR TRICERATOPS AND INTERPRETATIONS OF SENSORY AND MOTOR FUNCTION
Review round: 1
Reviewer: 2

Output:
Basic reporting: Language is clear and unambiguous for the most part. I've listed some spelling and grammatical issues that should be addressed but these are mostly a lot of little things.

The largest issue here is in Figure 7.

The caption says that this is the mean best hearing, but the X axis only shows the scaled and transformed endosseous cochlear length. There is no Y axis showing hearing frequency here. I would change out the graph for a XY graph showing the hearing frequency or swap it out for just a histogram showing scaled cochlear lengths in the various dinosaurs.

The rest of these are a list of minor requested changes

Line 49: Change "it is considered" to: "it was inferred".

Lines 53–54: Delete "thus". Move the rest of the sentence up to line 44 right after
"Napoli et al. 2019)".

Line 55, 69, and elsewhere: Delete the extra modifier "ceratopsids". You can just say "centrosaurines" or "chasmosaurines". The entire article is about ceratopsians and dinosaurs in general. The audience will know what groups you are referring to.

Line 59: change "Pachyrhinosaurus has" to "Pachyrhinosaurus had".

Line 60: Delete "Because of the" and start the sentence at "Elongate".

Line 61. End the sentence after "(Spoor et al. 2007)". Start next sentence with: "The authors".

Lines 63–64. Sentence:

"In addition, because Pachyrhinosaurus has quite a short cochlear duct, it was suggested that"

Change to:

"In addition, Pachyrhinosaurus had a short cochlear duct, suggesting that"

Line 70: change "can" to: "could".

Line 74: change "is" to "was".

Line 81: Delete "thus".

Line 83: Delete "dinosaurs". Can simply end with "ceratopsians".

Lines 100–101: The section that reads:

"including non-theropod dinosaurs"

I would rewrite it to just say:

"including most dinosaurs".

Incidentally, this endocast trend would extend down to the base of Maniraptora, as even tyrannosaur brains don’t fill the endocranial cavity.

Line 101: "does" is misspelled.

Lines 101–102: The section reading:

"Hopson 1979); therefore, it should be considered that endocasts do not provide"

I would rewrite it to be a bit more concise such as:

"Hopson 1979). Thus, endocasts do not provide"

Line 103: Delete "among these animals" and just end the sentence after "morphology".

Lines 104–105: I would rewrite this sentence to make it clear that endocasts are still important even if they are limited. Something like:

"Despite these limitations, endocasts still provide the best first-hand information on brain size and shape in extinct species."

Line 109: Delete "that was".

Line 116: Change "size" to "length".

Line 119: I would rewrite this sentence to make it flow a bit better. Something along the lines of:

"Following this, we use the body mass estimates for BSP1964 I458 (4963.6 kg) from Seebacher (2001), as an equivalent estimate for our two specimens."

Lines 143–144: I would change "mean hearing" to "mean best hearing" as described by Walsh et al. 2009.

Line 151: I’m confused by the statement: "As other dinosaurs". Does this refer to specific specimens? Was this meant to read "As with other dinosaurs"? If the latter, can we have a citation or two to verify the claim?

Line 157: Delete "the" in front of "Pachyrhinosaurus lakustai".

Lines 161–162: The last sentence reads strangely. I would rewrite it to something like:

"We also were unable to observe the optic tectum in our specimens."

Lines 182–186: This last section has a fair bit of redundant phrasing in it. As with lines 55 and 69, we can drop the extra modifiers here. You can compress things down a bit too without losing the meaning. For example:

"appear from different foramina, as is seen in other chasmosaurines such as Anchiceratops (Hopson 1979). This is in contrast to centrosaurines like Pachyrhinosaurus, which show the two trigeminal nerve trunks branching from the endocast in closer association (Witmer & Ridgely, 2008; Tykoski & Fiorillo, 2012)."

Line 207: To maintain consistency with the anatomical terminology, I would remove "just below the" and replace it with: "ventral to the".

Lines 219–220: Can rewrite the section after "Therefore" to say: "we assume both Triceratops specimens were around the same ontogenetic stage."

Line 229: Zelentisky is misspelled.

Line 231: Change "theropods and archosaurs" to "theropods and other archosaurs".

Lines 231–234: I would just state your estimated mass from your specimens. You already covered how you came to this mass estimate in your methods section. No need to repeat it here.

Line 264: I would remove "non-avian". The rest of the text uses dinosaurs in a paraphyletic context. Best to stay consistent.

Line  275: Change "Therefore" to "Similarly".

Line 280: Delete "Hence the" and just start the sentence from "CL".

Line 281: Replace "Hence" with "As".

Lines 279–284: I think this section would benefit from a figure call to justify the statement about hearing, or a mention of the range of best hearing for the specimens / species.

Line 283–284: Replace: "have had the ability to hear very distant sounds" with: "have been sensitive to more distant sounds".

Line 296: I would rewrite the start of the paragraph to make it more concise. Suggest:

"Based on our interpretations of the endocranial anatomy of Triceratops, we suggest that (1)"

Line 299: Would remove the bit about "pecking at grass". That, or replace with "pecking at flowers" (grasses not being prevalent at the time).

Line 300: You could expand some on #4 and state that evidence for low gaze stabilization suggests that rapid head movements were uncommon.

Figure 1 caption: Abducens nerve canal is misspelled.

Figure 7: Delete "non-avian".
Experimental design: There are some issues / questions about the methodology.

The olfactory ratios and mean best hearing abilities that are shown in the tables would greatly benefit from an extra column showing where the authors obtained their data. Some of these references (all?) are mentioned in the Materials and Methods section, but I'm still not certain exactly where some of the raw comparative data came from. I go into more detail on this in the Validity of the findings section.
Validity of the findings: There are some large issues with the reported data and some of the interpretations. These will need to be addressed before publication. In particular, the data presented in Table 3.

Table 3: There is something wrong with some of the values in Table 3. You can’t have negative values for hertz barring certain mathematical abstractions. The reported results are correct for Triceratops, Tyrannosaurus, and Gorgosaurus based on the Walsh et al. 2009 equation, but they are also impossible. I suspect that there was an error in the BCL measurements. However, it’s not possible to say for certain without knowing how the measurements were made and where the original data came from. The table needs either an extra column or footnotes by each taxon name listing where the measurements for each specimen came from. I believe that some of the references are mentioned in the Materials and Methods section (e.g., Evans et al. 2009; Witmer and Ridgely 2009), but at least some of these papers do not provide quantified measurements, so I’m not sure where the authors obtained their data. If they were acquired from the images in those papers, it should be mentioned in the methods.

A separate figure showing the criteria used for CL and BCL would be helpful here. Walsh et al. 2009 talk about their CL criteria, but they do not cover the BCL criteria. I’m assuming Walsh et al. followed in the vein of Radinsky (1985) and used the reptilian equivalent of the basioccipital and basisphenoid (i.e., straight-line distance from basal tuber to basipterygoid process as was done by Chure and Madsen 1996). If we go by those limitations, I get a BCL length closer to 100–150 mm for FPDM-V-9775, based on the supplied images. This results in a hearing range around 1530–948 Hz. However, if I use the equation from Gleich et al. 2005 (the one who started this whole trend), I obtain a best hearing frequency of 65 Hz.

Lines 110–111: The authors state that Anderson 1999 found a significant correlation between occipital condyle area and total skull length, but that’s not true. As Anderson 1999 wrote:

"Figure 5B shows the result, and indeed the r2 value (r2=0.732) is increased to a level comparable to that of B. vittatus. However, this result must be interpreted cautiously as the sample size is small (n =5) and the regression is not statistically significant (p ~0.064)."

If this is the best method available right now for ceratopsian head size then so be it, but the authors should mention the limitations of the Anderson equation and that their skull sizes are only rough estimates.

Lines 125–127: The authors used the olfactory ratio calculation method of Zelenitstky et al. 2009. This is another study that has important caveats associated with it that I think the authors need to mention in their study. Namely, Zelenitsky et al. focused only on theropods. Among extant archosaurs, they used a wealth of bird studies and only 3 alligator specimens. The project was very theropod focused and it showed in their results, as their alligator data all fell well above their regression line confidence intervals (though, to be fair, so did their tyrannosaur and dromaeosaur data). It’s likely that the equation that Zelenitsky et al. used is really only good for theropods. The results of this current study further corroborate this as nearly all the non-theropods fell well away from the regression line. I’m fine with the use of the Zelenitsky et al. study (especially since there is not much else out there), but I would make it clear to the audience that the equation used may not be relevant outside of Theropoda.

Lines 235–244: As with lines 125–127, I would stay cautious of interpretations of the results here, as the Zelenitsky et al. 2009 paper was very theropod focused.

Lines 285–287: I would be very careful about using the correlations from Walsh et al. 2009 like this. The authors did find a significant relationship between cochlear length and group size, but their r2 was very low (0.485), indicating that cochlear length is a poor predictor of group size. Low r2s are seen in all the Walsh et al. equations. As such, I would be cautious about any interpretations based on their formulae.

Extra references used in this review

Chure DJ, Madsen JH. 1996. Variation in aspects of the tympanic pneumatic system in a population of Allosaurus fragilis from the Morrison Formation (Upper Jurassic). JVP. 16(1):63-66.

Gleich O, Dooling RJ, Manley GA. 2005. Audiogram, body mass, and basilar papilla length: Correlations in birds and predictions for extinct archosaurs. Naturwissenschaften 92:595–598.

Radinsky, LB. 1985. Approaches in evolutionary morphology: A search for patterns. Ann Rev Ecol Syst. 16:1–14.
Additional comments: I think this is a solid paper that will contribute nicely to our body of knowledge on Triceratops and ceratopsians in general. I appreciate the push for quantification of the data as opposed to the more qualitative approaches done in the past. However, I do think that there are some problems with some of the reported data on hearing frequency that will need to be addressed before the manuscript can continue. Nothing requested should be hard to fix, and I don't suspect a long delay to 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: ENDOCRANIAL ANATOMY OF THE CERATOPSID DINOSAUR TRICERATOPS AND INTERPRETATIONS OF SENSORY AND MOTOR FUNCTION
Review round: 1
Reviewer: 3

Output:
Basic reporting: The draft is complete in structure and relatively easy to understand, but there are still some grammatical issues and ambiguous parts which need to be corrected or supplemented, especially the sections like ABSTRACT, RESULTS and DISCUSSION, please see the attached PDF.
Experimental design: This is a pioneering study on the quantitative analyses of the endocasts of ceratopsian dinosaurs, although the figures and tables are exquisite, the draft is not detailed enough, please add some information listed in the annotated file.
Validity of the findings: A few views or speculations don't make sense, some analogy are not very accurate, please explain them respectively.
Additional comments: Sorry I didn't revise the draft very carefully because the global virus epidemic, I hope all the people and countries can get through this incident safely. I have annotated some of my opinions in the PDF, and I would recommend publication of this manuscript after major 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: ENDOCRANIAL ANATOMY OF THE CERATOPSID DINOSAUR TRICERATOPS AND INTERPRETATIONS OF SENSORY AND MOTOR FUNCTION
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: Thank you to the authors for their thorough revision and accompanying explanation on the latest version of this manuscript. They have done a good job of addressing the major issues, and the paper is much improved. I have only a few minor follow-up comments/suggestions. I do not need to see the revisions, if any, for another round of review.

For FPDM-V-9677, can you indicate how well the estimated skull length matches with the reconstructed skull length? I recognize that the skull is missing some parts, but it would be a helpful check to see if it's consistent with the estimate from occipital condyle size.

Line 254: I would be cautious on assuming they are the same ontogenetic stage. This is potentially true, but alternatively they could be different stages with just the same braincase size. Given size, they're at least probably late subadult (using the terms from Horner and Goodwin 2006), but that's about as far as I would go with the evidence at hand. That said, I don't think this point has a major impact on the results or interpretations.

Line 280-281: Note that Marugán-Lobón et al. 2013 specifically expressed caution on interpreting head posture from semicircular canal position (see third paragraph of the discussion there, and other papers cited therein).

Regarding issues of allometry (e.g., accuracy of predictions for hearing frequency), I would suggest at least acknowledging the breadth of the potential confidence interval for these estimates once you are outside of the size range of the original data used to calculate the equation. Additionally, I would also suggest a brief acknowledgment of the complicating effects of body size in the analysis presented in Figure 6, and the use of ratios. I am still uneasy about how body size and locomotion/posture may be conflated here, although as long as the authors mention this possibility in the text as a possible future research avenue, I am OK with leaving it at that.


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

Input:
Title: ENDOCRANIAL ANATOMY OF THE CERATOPSID DINOSAUR TRICERATOPS AND INTERPRETATIONS OF SENSORY AND MOTOR FUNCTION
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The authors did a commendable job improving the manuscript and I think it is ready for publication. The only thing that I would recommend fixing is in line 54, which says P. Amitabha. The species name just needs to be put in lowercase (P. amitabha).


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: ENDOCRANIAL ANATOMY OF THE CERATOPSID DINOSAUR TRICERATOPS AND INTERPRETATIONS OF SENSORY AND MOTOR FUNCTION
Review round: 2
Reviewer: 3

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: I am happy with this work for the second time, which is much improved on the first version, including adding some basic decription and comparision. I feel only a little issues that require ironing out before it meets the baseline for publication, provided these are followed/engaged with, I see no reason why this work should not be published (and the figures are very nice).
I have no other technical problems with the manuscript, with my remaining concerns regarding the written English at some points, as well as some content from the response to reviewers that would merit a place in the manuscript. These requirements are not exhaustive and should not take long. I also wish to thanks the authors for the comprehensive responses to the previous reviewers' 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: GENETIC VARIATION AND SELECTION IN THE MAJOR HISTOCOMPATIBILITY COMPLEX CLASS II GENE IN THE GUIZHOU PONY
Review round: 1
Reviewer: 1

Output:
Basic reporting: The study revealed a high level of diversity present in the Guizhou ponies (GZP) through comprehensive analyses conducted on the MHC class II gene, and positively selected codons were mostly found in ABS, which are linked to the defense ability of GZP against foreign pathogens. In addition, both ancient and species-specific alleles were revealed in the gene regions, which shown evolutionary relationships of GZP with other ponies and horses, and genetic novelties gained during the evolutionary course of GZP since its separation with other ponies. These results are significant and meaningful for GZP evolutionary conservation, and values for considering GZP as unique genetic resources. For this reasons I would like to suggest its acceptance for publication on Peer J if they can address my following minor concerns and suggestions.
Experimental design: The data and analysis methods are solid, and the figures and tables are clear. English writing is also acceptable, albeit some small changes should be made.
Validity of the findings: For a long time, the unique genetic characteristics of GZP are unclear, and thus it is undervalued and frequently hybridized with other ponies. This is definitely deleterious to the genetic resource of this indigenous species in China. The genetic uniqueness revealed in this study is helpful to its  genetic conservation and to consider it as evolutionary significant subspecies.
Additional comments: 1, Line 27  I suggest to delete the “the pony” in “gene in the pony GZP”,  GZP means the pony. And the last sentence in the abstract should be polished.

2, Line 75-76, reference(s) should be added

3, Line 91, it should be clarified that how many individuals are represented by the 50 blood samples.

4, Line 102,  the related GeneBank sequences are not clearly clarified.

5, Line 152, what is the means of “1000 sequencing data”?  And you mentioned “the effective numbers of alleles were 118”, do you mean the rest 66 alleles are not effective? Why ？

6, Line 157 I just can’t get the point of “considerable sequence diversity within the same genus”. Do you mean that DQA/B, DRB harbor a higher level of sequence diversity than that in other species from the (Equus) genus? I did not find the comparative analyses on sequence diversity on DQA/B and DRB among the species within Equus genus.

7, Line 158-159 you mentioned “In contrast, DRA shown much lower diversity of nucleotides, which is consistent with the level of nucleotide diversity at genus of Equus (Kamath et al., 2011)”, according to my understanding, the diversity of nucleotides in DRA is much lower than that in DQA/B and DRB in GZP, which, however, is comparable with the level of nucleotide diversity in DRA from other species within Equus genus.

8, Line 168, “(38.10%) in DQB alleles”, I think you mean DRB here.

9, Line 176, I do not find the “Brown et al. 1993” in the Reference section.

10, Line 222-223, English writing need to be polished, such as “The variable evolutionary rates across codon sites (M3) provided better fit to the data than the M0 model” will be better in expression like “The variable evolutionary rates across codon sites (M3) fit the data better than the M0 model”.

11, Line 251, the subtitle is inappropriate, both selection and network analyses belong to Evolutionary analysis.

12, Line 284, the authors claim that they found elevated levels of diversity at DQA/B, DRA/B in GZP. However, I did not find any comparative analysis on the sequence diversity of DQA/B, and DRB  between GZP and other species except that DRA were compared with other horses, dogs, cats, goats and pigs.


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

Input:
Title: GENETIC VARIATION AND SELECTION IN THE MAJOR HISTOCOMPATIBILITY COMPLEX CLASS II GENE IN THE GUIZHOU PONY
Review round: 1
Reviewer: 2

Output:
Basic reporting: English: Low quality of English throughout the entire manuscript; sometimes difficult to understand what the authors want to say (e.g. two last sentences of Abstract). A revision by a native speaker is recommended.

Introduction: This part is not well structured, it does not provide a convincing rationale of the experimental design. To re-write it, reflecting the points below, would be a good idea.
- it contains incomplete and/or incorrect statements - information about the role of MHC genes in immune responses is not fully correct (line 46) and is very general (“initiation of immune response” – line 50); the professional terminology is not always appropriate (“polymorphism of MHC loci diversity”, line 54);
- differences in the function of MHC class I, II and III molecules are not explained; consequently, it is not clear to the reader, why just exon 2 sequences of MHC class II genes show the highest genetic variation (lines 52-53), why they associate with diseases (not only infections – line 55), and why they have been extensively studied in many vertebrate/mammalian species;
- therefore, their relevance for “evolutionary relevant and adaptive processes”, line 61 is not clear;
- the review of literature does include relevant recent information both on the MHC in general and on the MHC of the domestic horse and of other equids; consequently, the  experimental design is based on an obsolete concept (see below);

Structure of the manuscript: The paper has standard structure that conforms to PeerJ standards, including acknowledgments/funding information, ethical statements, declaration on competing interests and authors´ contribution. 11 figures and 2 supplementary tables were submitted as separate files. The supplementary tables were attached as Excell files. All figures are labelled and described. Their relevance is related to the limitations of the experimental design (see below). Sequence data are available in the Supplementary table 1. There is no information whether these data have been submitted to a repository, no accession numbers are available in the text.
Experimental design: Originality of the research:  The genetic diversity of MHC class II genes and their exon 2 sequences has been studied in many mammalian populations, including horses and other equids. The use of a local pony breed for this purpose represents an original aspect of this study, which is within the scope of the journal.

Research concept: The experimental design and the resulting research question are not based on a current knowledge of the genetic structure of the equine MHC. Important information, especially the data from Viļuma A, Mikko S, Hahn D, Skow L, Andersson G, Bergström TF: Genomic structure of the horse major histocompatibility complex class II region resolved using PacBio long-read sequencing technology. Sci Rep. 2017 Mar 31;7:45518. doi: 10.1038/srep45518, have not been taken into consideration, as well as the last assembly of the domestic horse whole genome sequence (EqCab3.0 – Kalbfleisch et al.: Improved reference genome for the domestic horse increases assembly contiguity and composition. Commun Biol. 2018 Nov 16;1:197. doi: 10.1038/s42003-018-0199-z. eCollection 2018. Erratum in: Commun Biol. 2019 Sep 11;2:342. Commun Biol. 2019 Sep 11;2(1):342.), where the MHC region has been quite well annotated. Other resources, such as Miller et al. (2017) were cited in the context of disease associations, but relevant information related to MHC class II genes was not fully explored. Currently, it is clear that in the domestic horse, the MHC class II region contains multiple DRB, DQA, and DQB genes, including some pseudogenes. Therefore, the major limitation of this manuscript is that it does not distinguish between individual genes. The primers used for amplifying DRB, DQA, and DQB sequences are not locus specific. As only one DRA gene has been identified in horses so far, this problem does not concern this locus. However, for DRB, DQA, and DQB genes, the overall data presented in the manuscript are necessarily biased. As there probably are differences in effects of selections on different loci (e.g. Janova et al. 2009, cited in the paper), this limitation is also important for the analysis of selection. The donkey whole genome sequence (Renaud et al. Improved de novo genomic assembly for the domestic donkey. Sci Adv. 2018 Apr 4;4(4):eaaq0392. doi: 10.1126/sciadv.aaq0392) shows a very similar structure of MHC class II region and multiple class II loci exist probably also in asses and zebras. Taken together, the interpretation of the evolutionary and selection analyses presented here is ambiguous and difficult to interpret.

Methods used:
Important information about the population sampled is missing. It is not clear to what extent the “randomly selected” ponies could be related, and what was the proportion between males and females.
Standard DNA extraction, PCR, and cloning techniques were used. There is no information on how Sanger sequencing was performed (outsourced?). Information on the location of the primers used is not available. Locus-specificity of the primers used has not been assessed.
Evolutionary analyses used standard tools. As for selection analyses, it is not clear how the PAML package was used, especially how decisions about selecting different models were made. Especially, it is not clear whether recombination was considered in this context. As pointed out above, both of these analyses are limited by the experimental design.
It is not clear how, based on HLA equivalents (lines 175-176), the antigen-binding site residues were identified. It seems that only one of the two references “Brown et al.” relates to this problem.
All these issues should be addressed to improve the manuscript. On the other hand, some of the data presented (e.g. Supplementary table 2) are not very informative for the purposes of the article.
Validity of the findings: The effort of the authors has undoubtedly brought information on novel allelic exon 2 sequences of MHC class II DRA, DRB, DQA and DQB existing in Guizhou ponies. As explained above, the interpretation of these data is limited by the experimental design for three out of four sub-regions. The authors do not say how many DRA, DRB, DQA and DQB sequences they retrieved from individual horses. This information would be very helpful for understanding which type of data they actually collected. The sequences obtained have not been deposited in public databases.
For all these reasons, an accurate and correct interpretation of data presented in the manuscript is really difficult, which is also a limitation for the value of Discussion, along with the quality of English.
Additional comments: The manuscript submitted brings new information on genetic variation in exon 2 sequences of MHC class II genes in a local pony breed. Some serious deficiencies across all its sections should be addressed before the data can be published. It probably would not  be enough to simply re-write it, but the data obtained could be re-analyzed. If done properly, at least one part of them could be published.
The authors could be encouraged for example by a very recent analysis of a DRB3 locus in cattle (Bohorquez et al Frontiers in Genetics, 2020). The authors also should pay attention to recommendations on comparative MHC nomenclature (Immunogenetics 70: 2018: 625-632).


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

Input:
Title: GENETIC VARIATION AND SELECTION IN THE MAJOR HISTOCOMPATIBILITY COMPLEX CLASS II GENE IN THE GUIZHOU PONY
Review round: 1
Reviewer: 3

Output:
Basic reporting: The paper must be checked carefully for grammatical errors but also for the general English terminology. I have provided some suggestions, but not for all the errors I have found. The general concepts in the introduction/background are quite exhaustive. In some cases, I have provided some suggestions for concepts that could be clarified and expanded as well as for missing references. Article structure appears appropriate, figure relevant to the content and appropriately described and labeled. The manuscript contains the proper analysis and results for the scope of the work and for a publication.
Experimental design: The work has rigorously performed, with scientific and methodological soundness. The aim of the paper was also clearly defined. Methods were sufficiently described with some missing information in the “samples PCR amplification, cloning, and sequencing”.
Validity of the findings: Data were robust and statistically sound. Conclusions were stated appropriately; however, some sentences should be phrased more clearly and improved.
Additional comments: Review on Genetic variation and selection in major histocompatibility complex class II gene in Guizhou pony

This manuscript aims at the characterization of the genetic diversity at MHC II exon 2 of DQA, DRA, DQB, and DRB regions in Guizhou pony (GZP). The relationship between the observed genetic variation at the MHC II of GZP and mechanisms of selection and evolution were also explored. Exon 2 regions of the ELA-DQA, DQB, DRA and DRB genes were amplified and sequenced from a total of 50 samples. Allelic and nucleotide diversity were explored and analysis of nucleotide and amino acid composition performed. Further analyses were performed to characterize the extent of the observed variability. Evidence for selection ware tested with different approaches: dN/dS ratio, Z-test of selection implemented in MEGA7 software. At the four investigated loci, site-specific selection analyses are provided by measuring the relative proportion of nonsynonymous and synonymous substitution along the full amino acid sequence as well as specifically in the antigen binding site (ABS) and non-ABS. Positive selection was further tested using CodeML subroutine implemented in PAML program. Finally, phylogenetic relationships among sequence haplotypes were defined by constructing median-joining haplotype networks. The work was rigorously performed, with scientific and methodological soundness. This study is relevant and shows interesting results. It provides a comprehensive characterization of the genetic diversity at MHC II exon 2 of DQA, DRA, DQB, and DRB regions in Guizhou pony (GZP). It reveals signatures of selection at the immunological relevant antigen binding site (ABS). It gives an interesting overview of the phylogenetic relationships between the Equine leukocyte antigen (ELA) haplotypes. Finally, the manuscript provides a basis for further in-depth investigations on how the observed signatures of selection could be linked to the pathogenic environment to which Guizhou ponies are exposed in the Guizhou province of China.

General comments:
The English language should be improved to ensure that an international audience can clearly understand your text. Some examples include lines 38, 49, 65, 66, 72, 76, 79, 118, 207, 322, 349, 362, 366 – the current phrasing makes comprehension diﬃcult.

L38 I suggest improving the description of lines 38-40. Here, a clearer sentence could highlight the importance of your work.

L46 The major histocompatibility complex (MHC) genes are very well known for their role in adaptive immunity. If you don’t want to be specific then I suggest keeping this sentence general; something like “The major histocompatibility complex (MHC) genes play a major role in vertebrate immune systems”.

L49 Please consider exchanging: “The MHC class II is highly polymorphic cell-surface molecules”: with “The MHC class II are highly polymorphic cell-surface molecules”.

L64 In this sentence I think you can add some more species (and corresponding references) as the mechanisms you are referring have been extensively studied in many other species as well. For instance: correlative and experimental support for the negative frequency-depend selection at MHC genes has been provided in humans (Trachtenberg et al. 2003), reed warbler population (Westerdahl et al. 2004), laboratory mice (Kubinak et al. 2012), stickleback (Eizaguirre et al. 2012; Bolnick and Stutz 2017) and guppies (Phillips et al. 2018). Examples of asymmetric overdominant selection have been showed in a number of natural and laboratory populations (Landry et al. 2001; Richman et al. 2001; Lenz et al. 2009; Schwensow et al. 2010; Lenz et al. 2013), and supported by several computer-based binding prediction studies (Lenz 2011; Lau et al. 2015; Buhler et al. 2016; Pierini and Lenz 2018).
Also, I would suggest some small gramma changes to make the sentence more appropriate “It has been extensively studied that the mechanisms of negative frequency-dependent and over-dominant selection maintain diversity at MHC genes in …”.

L65 I am not familiar with the term “primary of evidences” please consider exchanging with: “primary sources of evidence”.

L72 “In the family Equidae, the horse MHC class II gene, ie. Equine leukocyte antigen (ELA) class II, located on the short arm of chromosome 20q14-q22” I suggest changing with “In the family Equidae, the horse MHC class II gene, i.e. Equine leukocyte antigen (ELA) class II, is located on the short arm of chromosome 20q14-q22”.

L75 Which are the previous studies? Please provide the proper references. Also in this sentence be sure to clarify and distinguish between the peptide binding groove and the antigen binding site (ABS). Exon2 code for a part of the pocked of the MHC molecules, within this sequence some of the amino acid residues are called antigen binding site (ABS), which are the residues rich in genetic variation (where the nonsyn mutations are observed more often than the syn) and, as you well clarify in the results, those which are thought to be the position in contact with antigens peptide.

L76 “The DQA and DRA encoded the α-chain of ELA class II molecule, and extensive polymorphism of DQA and DRA genes have been determined in European equids” I suggest to change with “The DQA and DRA genes encode for the α-chain of ELA class II molecules, and extensive polymorphism of DQA and DRA genes have been determined in European equids”.

L79 Similar to previous please consider to change the sentence with “The DQB and DRB genes encode the β-chain of ELA class II complex, and high level of DRB and DQB polymorphism have been reported for Arabian and European horses”.

L83 Why did you add this sentence about the body height? There is something relevant about this phenotype? Form my naïve point of view would be nice if you can add why this is important.

L101 If possible please provide the reference for the Primer 5 software.

L103 I am not familiar with the way in which you report the PCR details. Could you, for instance, specify the concentration and type of the different reagents in detail (buffer, dNTP, polymerase, and primers)?

L118 I have the feeling that a part of the verb is missing in the sentence.

L189 The first sentence of this paragraph is not very clear “not all the variable amino acids were selected”. I am not familiar with this test but, is the Wu-Kabat index a test for selection? or is a measure for variability that can elucidate positions that are more variable in your comparisons? Introducing the Wu-Kabat index could be very helpful for the readers.

L207 Please consider exchanging with: Our data are in agreement with results observed in the Argentine Creole horse, which exhibited rate…

L216 I think it is better if you report the actual p-value in text and not only in the table, as you did for all the rest of your analysis.

L309 Can you speculate why there is low variability in the DRA locus but you still find nine DRA codons under significant positive selection?

L322 Please consider exchanging: “the evolution relationship” with “the evolutionary relationship”.

L347 I think this sentence is very interesting for the results of your study and you could expand it. For instance, could you explain what “be evolutionarily old enough” means and/or what this implies?

L349 I really enjoy your discussion. I can suggest some small changes “Furthermore, some unique haplotypes of GZP appear gradually in the evolutionary process, and may have a changed under local environmental pressures such as the unique set of pathogenic microorganisms present in the mountainous and humid districts in Guizhou province, China.”

L362 please check separat

L366 I don’t get the meaning of the term crowns here, please check. Also, I would suggest some small changes “Meanwhile, a fairly large number of unique haplotypes dispersed in GZP crowns might have been acquired in the long process of ELA molecule evolution.”

L366 I suggest adding a sentence on to how the study contributes to filling the gap of knowledge in the field.

L559 In Table 4 I cannot find the P capital letter as parameter indicating number of free parameter in the ω distribution. Please double-check this part; as you clam that small p indicates the proportion of site under each (ω) site class.

L631 In Figure 5 I guess the colors here are also indicative of the proportion of time each allele is found in the different species. If yes I think could be good to explain it in the legend.


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

Input:
Title: GENETIC VARIATION AND SELECTION IN THE MAJOR HISTOCOMPATIBILITY COMPLEX CLASS II GENE IN THE GUIZHOU PONY
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Thank you very much for all the modifications.
The paper is significantly improved after the changes.
L40 I think the sentence is incomplete.
I would still recommend including a description of the ABS sites in the introduction.


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: LIFE-HISTORY TRAITS AND INTRA-COHORT DIVERGENCE OF CLEARHEAD ICEFISH (PROTOSALANX CHINENSIS), INDICATING CANNIBALISM INCREASED FITNESS
Review round: 1
Reviewer: 1

Output:
Basic reporting: .
Experimental design: .
Validity of the findings: .
Additional comments: Manuscript review

“Life-history traits and intra-cohort divergence of clearhead icefish(Protosalanx hyalocranius), indicating cannibalism increased fitness”

Fujiang Tang, Wei Liu, Jilong Wang, James Henne

When working with noodle fish, the presence of two size groups (cohorts) is noteworthy. Noodle fish is a monocyclic short-cycle species of fish that lives only one year and dies after spawning. The authors convincingly showed that the difference in growth rate is associated with a difference in the nutrition of fish. Fish that feed on individuals of their species have a higher growth rate than fish that feed on zooplankton.
The conclusions of the work correspond to the task. The results of the work are convincing and allow us to evaluate the reason for the appearance of two size cohorts in the noodle fish population of Khanka Lake.
This manuscript is written in fairly high quality and can be accepted for publication, but there are a number of comments and inaccuracies to it, which, in my opinion, should be eliminated.

Remarks.

1. Line 3 onwards. The name of this species used in the article is outdated. It is currently the junior synonym for the species Protosalanx chinensis (= Protosalanx hyalocranius). In this regard, it is necessary to bring the name of the species in line. Look site online Eschmeyer's Catalog of Fishes California Academy of Sciences (http://researcharchive.calacademy.org/research/ichthyology/catalog/fishcatmain.asp).

2. Line 73. The water level area in Khanka Lake is variable and varies from 3940 to 5010 km2. The long-term average water level is 4070 km2 with an average depth of 4,5 m. Since 2010, there has been an increase in the water level in the lake. This is not noted in the present work and references to the literature from where the data are taken are not given.

3. Line 74. Khanka Lake is not located in the upper reaches of the Ussuri River. It is located a little in the middle of the river and connects to the Ussuri River through the Sungacha River. The upper reaches of the Ussuri River is located on the slopes of Snezhnaya Mount, located about 200 km southeast of Khanka Lake.

4. Lines 77-78. Not exactly understandable and inaccurate phrase. Perhaps it should have been written that in 1996, an international Russian-Chinese reserve “Khanka Lake” was formed on Khanka Lake on the basis of the Khanka State Reserve (Russia) and the Xingkaihu Nature Reserve (China).

5. Line 79. To make it clear where the samples were taken, it was necessary to write: “in the northwestern part of Khanka Lake near the locality of Dangbi”.

6. Line 86. Not the “width” of the net, but the “height”.

7. Line 89. Not the “depth” of the branchial network, but the “height”.

8. Line 93. Not the “depth” of the branchial network, but the “height”.

9. Line 99-102. Not entirely accurate description. Males differ from females in the structure of the anal fin, the same picture is observed in capelin.

10. Line 171. This part of the work does not take into account the fact that Khanka Lake is a very large body of water. The sampling site on the Chinese side is located in the deep part of the lake. If we assume that the first fast-growing cannibal fish cohort spawns in January-March, then, according to Russian residents, spawning fish are caught in bulk in May in rivers in the south of the lake. This is most likely the second, slowly growing cohort. In this regard, the proportion of females in the north of the lake is reduced due to active migration to spawning sites in the southern part.
However, this work (of the Chinese-Russian specialists) needs to be carried out comprehensively throughout the lake, as This issue has not been closed. The authors reflected in the manuscript what they observed in their part of the lake.

I hope that the work of the authors in this direction will be continued and reflected in new articles.

Head of the Laboratory
of Biological Resources
of Continental Waterbody
and Fish of Estuarine Systems
Pacific Branch “VNIRO” (“TINRO”), PhD                                Evgeny Barabanshchikov


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: LIFE-HISTORY TRAITS AND INTRA-COHORT DIVERGENCE OF CLEARHEAD ICEFISH (PROTOSALANX CHINENSIS), INDICATING CANNIBALISM INCREASED FITNESS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall, this reads well. One exception is the ambiguous terminology applied for maturity classification, which on l. 108-109, it is only stated that “Stages of maturity were classified into six phases according to Sun (1985).” Sun (1985) does not come up in an internet search, so it is not accessible, and thereby it is not possible to examine whether it conforms with newer practices (e.g., Brown-Peterson et al., 2011;  DOI: 10.1080/19425120.2011.555724 or McBride et al. 2015; http://dx.doi.org/10.1111/faf.12043). Worse, in the manuscript, the maturity stages in Figures 4 and 7 are numerical, without any label or context. I would recommend that labels are associated with the Roman numeral classes of maturity and some attempt is made to show that this scheme still makes sense relative to newer references. The same can be said about phases of the oocytes, although these at least have labels associated with them (e.g., l 177-8)
Experimental design: This paper employs a complementary set of relatively simple methods. Nice job. I thought carefully about the potential for different selectivities of the multiple gears. This could perhaps be addressed more directly by the authors, but I don’t see that any problems would emerge from a more sophisticated analysis. The sampling frequency is good.
Validity of the findings: I am not so sure about your conclusion that oocyte development in asynchronous. That is unlikely for a semelparous fish (see for example McBride et al. 2015; http://dx.doi.org/10.1111/faf.12043. More likely, in Fig. 5, there are a mix of closely related oocyte phases early in development (5a) but these become more of a single, advanced phase closer to the spawning event. I encourage you to look closer at your data, examining a few more samples as appropriate, to reach your conclusion about the synchrony of oocyte development in ice fish.

I would be careful about confusing reproductive investment (e.g., GSI) or reproductive potential (absolute fecundity) with fitness (at least defined as producing offspring that go on to reproduce themselves). Do you know anything about the breeding system? Here is one possibility: What if the small males can ‘sneak’ in on a broadcast spawning event and successfully fertilize eggs? There are many other possibilities. I like the system you have revealed to me here, but to address the fitness issue more work is needed, like a parentage assessment.

You mention that these results suggest ‘evolution towards early birth and faster growth’ (l. 265). Perhaps, but if so, is warming occurring over time in your region and how may this accelerate or dampen this possibility. Also, consider that the constant sex ratios early on, preclude environmental sex determination from causing your patterns of size and sex (e.g., Conover 1984; https://www.jstor.org/stable/2461097). You might want to mention that.
Additional comments: l. 58, 64, 81, and throughout: put the species name in Italics

l. 63 define ‘hierarchical growth’ and put it in context

l. 114 What stage(s) were these oocytes that were counted? Are you counting only a specific stage (e.g., vitellogenic) or multiple stages (e.g., the leading size cohort)?

149-150 there is something wrong with this text “the LS distribution pattern was unimodal (range, 10-20 mm) until early July,” What is LS (SL?) and is that range correct?

l. 170 you refer to only natural mortality here. Is that true: that is, there is no direct icefish fishery or bycatch fishery from some fishing gear in this lake?

Fig. 3. What are the arrows in a-d?

Fig. 7. Should ‘b’ be the upper modal group (not lower)?


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: LIFE-HISTORY TRAITS AND INTRA-COHORT DIVERGENCE OF CLEARHEAD ICEFISH (PROTOSALANX CHINENSIS), INDICATING CANNIBALISM INCREASED FITNESS
Review round: 4
Reviewer: 1

Output:
Basic reporting: .
Experimental design: .
Validity of the findings: .
Additional comments: Everything is fine, the authors corrected the comments. The article is good, I hope that the authors will continue to study the life cycle of this species of fish.


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: LIFE-HISTORY TRAITS AND INTRA-COHORT DIVERGENCE OF CLEARHEAD ICEFISH (PROTOSALANX CHINENSIS), INDICATING CANNIBALISM INCREASED FITNESS
Review round: 4
Reviewer: 2

Output:
Basic reporting: see below
Experimental design: see below
Validity of the findings: see below
Additional comments: This is an improved draft but I still have some concerns, outlined below, that the authors should address before going to print.

l. 66-67 This sentence (Size-frequency …as growing (Zhu 1985)) is better but could be improved. How about: “The size-frequency of the population becomes bimodal from Month to Month” or “The size-frequency of the population become bimodal during Name the season, when the fish are approximately X-X months old” citing Zhu 1985.
l. 193-203 I still believe you are describing that the oocytes develop synchronously. I understand that they are not advancing together—all at once—from one stage to the next. That would be unexpected for two reasons: 1) the stages are a rank variable system that describes what is fundamentally a continuous process, and 2) there are minor deviations between germ cells in their rate of development. Instead, what you are describing here is likely a continuous, normally-distributed mode of oocytes that advance together (synchronously). For example, in Figure 6, the proportion of pre-vitellogenic cells (Pp) is declining at a linear rate because the tail of the normal distribution is becoming smaller and smaller in a gradual manner. In terms of testing the hypothesis of asyn- versus synchrony, it is not necessary for the decline in Pp to occur all at once for it to be synchronous. This difficulty in distinguishing asyn- from synchronous development is the authors do not plot the oocyte diameter frequency. Again, look at McBride et al. (2015; attached) in Figure 3 for the expected differences in oocyte diameter distributions between these two types of oocyte development.
l. 207 Is P really equal to 0? More likely it is < 0.001
l. 211 I am not convinced that the decline in pre-vitellogenic oocytes means that the fish will spawn in a single spawning event. It is still possible that vitellogenic ooyctes will mature and ovulate in multiple batches. Instead, if you are really seeing a depletion of pre-vitellogenic oocytes, that likely means this fish is semelparous because it does not maintain a reservoir of pre-vitellogenic oocytes for future years of spawning. Again, see attached, McBride et al. (2015) Figure 3 for an example.

-Richard McBride


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: DIFFERENT RESPONSES OF PLANT N AND P RESORPTION TO OVERGRAZING IN THREE DOMINANT SPECIES IN A TYPICAL STEPPE OF INNER MONGOLIA, CHINA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The language is a bit redundant, not standard English, and at quite many occasions, there are repetitions especially in Results section, e.g., the sentence in Line 229-230 is repetitive to the sentence in 208-209, and also to line 218-219. The article is self-contained, and has included sufficient introduction and background to demonstrate how the work fits into the broader field of knowledge. The structure of the manuscript conform to the acceptable format of "standard sections"
Experimental design: The manuscript presented an Original primary research within Aims and Scope of the journal. Research questions were well defined,relevant and meaningful, but with improper expression therein: in the first question, "changes in" should be deleted, because what the overgrazing altered is N and P concentration and resorption efficiency, as presented in the results section, not their changes.  Moreover, it was stated (Line 54-55) how the study fills an knowledge gap.
Methods described with sufficient detail & information to replicate. However, the investigation fall short of the pseudo-replication in the experimental plots designing, which is the biggest problem of the study.
Validity of the findings: Some results are contradictory. e.g., Line 218-220, here it was mentioned that grazing decreased NRE of C. squarrosa, but in line 212, it was meant that grazing increased its NRE.
The conclusion is merely repetition of results.
Additional comments: The topic of overgrazing effect on nutrient resorption is interesting and of significance for nutrient cycling research and grassland management. However, My major concerns include the pseudo-replication of the experimental designing. Another one is that, In the discussion and Conclusion, the authors claimed that leaf N and P in the green and senesced leaves determines the nutrient resorption efficiency, but that  was not the underlying mechanisms in terms of biological or ecological processes, but such determination was already in the formula calculating the nutrient resorption efficiency, i.e, it is just mathematical determination. I suggest the authors to discuss the discrepancies between the three species in nutrient resorption from the perspectives of their difference in biological features and adaptive strategies, thereby validate the inclusion of these three plant species in this article. By the way, in the Method section, you should explain why you choose these three species, and introduce a bit the biological features of the three species as a background information.


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: DIFFERENT RESPONSES OF PLANT N AND P RESORPTION TO OVERGRAZING IN THREE DOMINANT SPECIES IN A TYPICAL STEPPE OF INNER MONGOLIA, CHINA
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: General comments:
Wang et al. examined the resorption of N and P by plants of three grassland species in two contrasting communities (overgrazing site vs. grazing exclosure) in Inner Mongolia grassland. They found that grazing resulted in increases in the concentrations of N and P in green leaves and in the leaf N resorption efficiencies of Leymus chinensis and Stipa grandis but not in Cleistogenes squarrosa. They demonstrated that grazing was the primary factor leading to changes in N resorption efficiency for three species but only directly affected P resorption efficiency for S. grandis. They concluded that effects of grazing on different species were associated with their dynamics nutrient resorption efficiency due to variation in forage quality.
Overall, I think this is an interesting study on an important issue about how grazing affects the nutrients cycling processes in grassland ecosystems. The manuscript was well organized. Data analysis seems to be adequate, and results are well presented. However, the Discussion section needs to be improved.
I have several concerns on the Discussion and Conclusion Sections. First, the leaf concentrations and resorption efficiencies of N in Leymus chinensis and Stipa grandis were enhanced by grazing. This is an important finding of this study because these two species are widely distributed in Eurasia steppe, the largest grassland in the world, however, the explanation for this point is not sufficient, especially not associated with the physiological characteristics of these species. Second, based on the results of structure equation model analysis, grazing had strong direct effects on N and P resorption efficiency of S. grandis, but only had strong direct effects on N not on P resorption efficiency of L. chinensis. Why? They should give some explanation, at least some possible mechanisms, for these differences in Discussion Section. Third, in the end of Abstract, they suggested that effects of grazing on different species are associated with their dynamics nutrient resorption efficiency due to variation in forage quality. This conclusion has not sufficient evidence support by the results in this study. They did not examine the forage quality of each species. For the conclusion sentence, they should focused on the new findings of this study rather than over explanation. Finally, they used too many abbreviations that restricts the understanding by a reader.

Minor points:
Line 26: enclosure or exclosure ? please use the same word.
Line 29: C. squarossa, here you should use the full Latin name.
Line 86: three plant groups or three plant species?
Line 122: how did you place four 1 x 1 m2 quadrats in three 1.5 x 1.5 m cages?


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: POTENTIAL COVID-19 PAPAIN-LIKE PROTEASE PLPRO INHIBITORS: REPURPOSING FDA-APPROVED DRUGS
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The authors report that some commercial drugs are potential COVID-19 inhibitors using docking as a screening tool. The works is well addresses, nonetheless some comments should be kept in mind:

1) Line 63: add reference (see https://www.who.int/docs/default-source/coronaviruse/situation-reports/20200709-covid-19-sitrep-171.pdf?sfvrsn=9aba7ec7_2).

2) In the Methods section, the authors should provide the center and size (x,y,z) for the coordinates of the docking.

3) Current clinical therapy for COVID-19 is based on chloroquine, hidroxichloroquine, ivermectin  and azithromycin. The authors should provide a discussion of the bonds formed and differences in the binding site of any of these compounds against the compounds found to be the best in docking to corroborate that they are better than the drugs used in clinical practice.


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: POTENTIAL COVID-19 PAPAIN-LIKE PROTEASE PLPRO INHIBITORS: REPURPOSING FDA-APPROVED DRUGS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript discuss the discovery of new COVID-19 inhibitors. It is timely and important topic. However, Major concerns stands against positive response to the manuscript.
Experimental design: .General concerns
•	The study focused on docking studies. However, Docking alone is not predictive to binding efficiency
•	It is better to provide biological activity of the top 2-5 compounds
•	MD simulation must be done including RMSD comparison, RMSF for residues, radius of gyration, mass movement and entropy dissection. MD is the most robust computational tool for detecting drug-protein complex stabilities.
•	Rerank the compounds according to MMPSA /MMGBSA calculation and discuss the results in the light of it
•	The used dataset is not well justified , especially the source of compounds and their molecular descriptors
•	Provide the mutagenicity and carcinogenicity report for the compounds using the Korean Preadmet server
Validity of the findings: In Methods
I cannot understand how a pharmacophore model was generated from a structure does not contain any ligands. The used structure 6w9c is an Apo form of PLpro. Instead, the authors must reanalysis the pharmacophore model by using the new PLpro structures with modified amino acids ligands as 6WX4.
MOE was used in pharmacophore modeling, while autodock vina was used for docking. It is better to use MOE also in docking as it gives accurate results.
in results
The energy scores in Table 2 indicates few moderate binding compounds and the others are weak compounds
In Table 2, what are the clusters hh, jj, dd and S?
Discuss your finding in the light of previous PLpro virtual studies e.g. Pubmed PMID: 32597315, 32637945
Additional comments: Lines 40-42 are not accurate. The term protease comprises several families of proteins of diverse structure and function. The mentioned compounds must be accurately allocated to its corresponding protease e,g, Mpro, Plpro, …etc
Lines 44-45. These are host proteases. They also must be precisely described e.g. serine protease, …etc
Line 47: “Both proteases are highly conserved domains”  it must be corrected , what is meant by domains?
Lines 51-55, mention the number and location of ORFs cut by PLpro.
Figures 1-8 can be merged into one file
Figures 9-10 could be moved to supplementary materials


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: POTENTIAL COVID-19 PAPAIN-LIKE PROTEASE PLPRO INHIBITORS: REPURPOSING FDA-APPROVED DRUGS
Review round: 1
Reviewer: 3

Output:
Basic reporting: Kouznetsova and co-authors present a nice study of a combination of ligand- and structure-based in silico approaches for the discovery of SARS-CoV-2 PLpro  inhibitors.
The manuscript is a concise and very well written. The study showed the possible impact of massive computational power that a supercomputer can offer to researchers.
In my opinion, despite the absence of experimental validation of the identified hits, the paper give some nice insights into potential drugs that can be of use in compacting the current COVID-19 pandemic.
I have only a minor comments on the resolution of the protein structure used in the study (2.7A), the authors are advised to mention the resolution and comment on that such resolution although not optimal for computational efforts, it is of acceptable quality.
I recommend publishing the article in its current form.
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: RADIOLARIAN ASSEMBLAGES IN THE SHELF AREA OF THE EAST CHINA SEA AND YELLOW SEA AND THEIR ECOLOGICAL INDICATION OF THE KUROSHIO CURRENT DERIVATIVE BRANCHES
Review round: 1
Reviewer: 1

Output:
Basic reporting: English:
Not too bad but difficult to follow in parts.  I have made many comments on the attached pdf.
The paper is probably rather too short but more detailed explanation will help.

References:	Sufficient

Article Layout: Poor
o	Subheadings not easily distinguishable from the body of the text.
o	Lack of new paragraphs.
o	Some unnecessary repetition.
o	Probabilities quoted as “p < “ do not meet PeerJ standards.

Figures:
Inadequate and sometimes illegible labeling in figures 1-3; otherwise ok.

Tables:
Fine except that amalgamating Supplementary Tables 2 and 3 would make it easier to understand the discussion in the text.

Overall:	Self-contained

Other:
Many examples of mixed fonts, mainly (solely?) in species names.  This is 		almost certainly due to copying from the radiolaria.org website.
o		Genera & species names should be in italics.
o		Lipmanella dictyoceras (Haeckel, 1861) occurs twice in both Supplementary 	Tables 2 & 3.  In Table 3 the census results for the two entries for this species differ - should one of be a different species?
Experimental design: Experimental design

Journal Fit:
Within PeerJ Aims & Scope

Research Question:
Adequate statement.  The research is a sensible addition to the body of oceanographic knowledge but is local, rather than global, in its scope.

Investigation:
Fairly standard.  Some degree of “overkill” in the number of diversity indices calculated – one or two would have been plenty.

Methods:
Description definitely inadequate.  I ran the cluster analysis, the detrended CA, & the RDA but failed to reproduce the authors' results (although my answers were in the same ballpark).  Consider that, in addition to their raw data the authors should include a Supplementary Table containing exactly the data they tested & should provide all the parameters they used.  The authors used commercial software so should be able to provide all the input parameters.
Validity of the findings: Data:
Not provided in a form which would allow replication.

Conclusions:
Many examples of assuming causation from correlation or similar statistical evidence (e.g. line 233 “Silt percentage significantly affected the radiolarian species composition in study area.”; also lines 223 & 231).
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: RADIOLARIAN ASSEMBLAGES IN THE SHELF AREA OF THE EAST CHINA SEA AND YELLOW SEA AND THEIR ECOLOGICAL INDICATION OF THE KUROSHIO CURRENT DERIVATIVE BRANCHES
Review round: 1
Reviewer: 2

Output:
Basic reporting: The author provide a good report about radiolarian assemblages changes in the Yellow Sea and the East China Sea and they tried to explain the difference in radiolarian assemblages by a different ecology of the local water masses (Salinity, Temperature...). Thus, it an interesting report.
Experimental design: The design is good and follow the standard methodology and the authors did a considerable effort doing statistical analysis. This is also good.
Validity of the findings: The finding are good and the method also. However, I have seen some discrepancy in the interpretation of Tetrapyle inside their own manuscript and there is also some statistic concerns.

I wonder if the authors checked the multiple collinearity between the environmental variables prior other statistical analysis. Thus, I suggest to revise this issue as it can highly affect the discussion.

The relationship between Tetrapyle and Salinity should be revised as two opposite interpretation is proposed in the manuscript and may lead some confusions.

There is one important taxonomic error, which may affect the discussion. S. resurgens showed by the author is S. biconcavus. This is a concern because S. resurgens inhabit temperate water while S. biconcavus warm water. In addition in the present manuscript, this species group is a dominant species thus, the interpretation may have to change. I suggest to carefully check the spongodiscus data (re-count just this group) and revise it.

Therefore, I think that major revision is most suitable for this time because there are some important things to clarify about the Tetrapyle ecology, and the authors should clarify if Salinity and Temperature are collinear or not.
Additional comments: MS number: 44305
Authors: Hanxue Qu et al.,

The authors discuss changes in radiolarian assemblages in the marginal seas of the Northwest Pacific focussing on the Yellow Sea and East China Sea (Southern and Northern part). Their results are interesting and are helpful for the community of radiolarian paleontologist. However, there are several concerns in the data interpretation, which must be fixed before publication. Thus I recommend major revisions.

Major concerns:

1/ The authors investigated changes in radiolarian assemblages in the East China Sea and in the Yellow Sea, with many samples collected from the Continental Shelf. This area has a shallow water depths and thus the preservation of radiolarian is not good. Thus, as they showed in their supplements, there are a lot of station where radiolarian assemblages is composed of less than 100 specimens. They have neglected those samples from their study, which is good. However, I do not think that it is meaningful to estimate the diversity index in such area because you automatically, you will have a higher diversity in samples where you have counted 300 than in those you counted 100. Thus the proposed index is highly biased. It may be good to provide some assumption and show that you are aware from this issue.

2/ The authors did an effort carrying statistical analysis, which is good. However, it was ambiguous in the text and I did not understand if the authors checked the multiple collinearity between the environmental variables they used (SSS, SST, Grain size, chlorophyll…). This stage is crucial as the authors want to explain changes in radiolarian assemblages based on the 6 environmental variable they retained. I recommend to check first if there is any multiple collinearity in the retain variable by providing a table where the VIF is shown for each. I particularly want to see if the SST and SSS have a multiple collinearity or not. If they are collinear thus the proposed discussion should be modified and say that radiolarians seems to be control by a SSS-SST package hard to be dissociated. If they are really independent variable thus the discussion in it current form is fine.

3/ Interpretation of Tetrapyle spp.: The authors say that Tetrapyle is related to high SSS in the results, however in the discussion they say the Tetrapyle is dominant in an area where you have a mix of fresh water from the Yangtze Rivers discharges with the Kuroshio Current. This is strange as fresh water will diminish the SSS and thus if Tetrapyle is a high SSS marker it should decrease. I think that a careful check in the collinearity between SSS and SST must be done and also a more comprehensive review must be done about Tetrapyle spatio-temporal distribution. Indeed, they also claim that Tetrapyle is a marker of cold water tongue. This is also a strange statement as all the papers published until now shoed that Tetrapyle % increase during interglacial period during the Quaternary in the Japan Sea and in the East China Sea. Please check the paper below:

Matsuzaki, K.M., Itaki, T. and Tada, R., 2019., Paleoceanographic changes in the Northern East China Sea during the last 400 kyr as inferred from radiolarian assemblages (IODP Site U1429). Progress in Earth and Planetary Science, v. 6., no.22, pp. 1-21

Itaki, T., Sagawa, T., and Kubota, Y., 2018. Data report: Pleistocene radiolarian biostratigraphy, IODP Expedition 346 Site U1427. In Tada, R., Murray, R.W., Alvarez Zarikian, C.A., and the Expedition 346 Scientists, Proceedings of the Integrated Ocean Drilling Program, 346: College Station, TX (Integrated Ocean Drilling Program). doi:10.2204/iodp.proc.346.202.2018

Thus re-thinking is probably needed.

4/ There is a major taxonomic error about S. resurgens. The photo showed here indicate that what the authors called S. resurgens is S. biconcavus. This is a concern because S. resurgens is more likely a temperate to cold water species while S. biconcavus inhabited warm area. I recommend to check carefully the counts about spongodiscus species and re-think the interpretation.

Minor concerns:

L.29-31: Should be re-phrased. I do not understand the meaning.

L. 35: I suggest to check the paper of Suzuki (2016,The statistic information on radiolarian studies based on PaleoTax for Windows, a synonym database:  Fossil, 99，15‒31). There is more than 1000 species in modern ocean.

L. 37: I also suggest to have a look on Lombard and Boden 1985 Atlas. Reference: Lombari, G., G. Boden (1985), Modern radiolarian global distributions. Cushman Foundation for Foraminiferal Research, Special Publication 16A, 68-69.

L. 38: This is not a representative paper for radiolarian dissolution. I suggest to check:

Takahashi K, (1981) Vertical flux, ecology and dissolution of Radiolaria in tropical oceans: implications for the silica cycle (Doctoral dissertation, Massachusetts Institute of Technology and Woods Hole Oceanographic Institution). DOI:10.1575/1912/2420, https://hdl.handle.net/1912/2420

L. 40: There is more paper about that showing good schemes, see also :

Abelmann, A., Nimmergut, A. (2005). Radiolarians in the Sea of Okhotsk and their ecological implication for paleoenvironmental reconstructions. Deep Sea Research Part II: Topical Studies in Oceanography, 52(16), 2302-2331.

L. 49-51: I do not understood well. The KC do not enter the Yellow Sea but the coastal warm current which bifurcate from Taiwan Warm Current is. So perhaps also look at the book below where the oceanography is described easily for a general scientific audience:

Tomczak, M., Godfrey, J.S. (1994). Regional Oceanography: an Introduction. Pergamon Press, Oxford, 1-422.

L.68-72: What you say is the true, but Chen & Wang, 1982; Tan & Su 1982 are both excellent taxonomically so it may be good to say that they are amazing taxonomic works.

L.73-77:  I recommend to focus on clarifying changes in radiolarian assemblages among both sea, which can be explain by changes SST, SSS… It is better to be more focussed on your assemblage data. Otherwise we get lost in your objectives.

L. 88: Canada gum-> Canada balsam

L. 100-1001: Is that a 1° interpolation?

L. 106-114: See my major concern 1 above.

L. 118: it is better to add  "for normalize the dataset » after square root.

L. 128-129: I think it is related to my major comment 2. The VIF mean that you check the multiple collinearity between the environmental variable? If so please show all the results in the main text and explain why you took the threshold of VIF>10 usually it is 5 based on Lomax, R. G., & Hahs-Vaughn, D. L. (2012). An introduction to statistical concepts (3rd ed.). Routledge/Taylor & Francis Group.

128-129: Please show data if you want the neglect it.

L. 156: I understand the meaning but please re-phrase it with word.

L. 161-163: Again I am not sure how much is the diversity index suitable in this context.

L. 171-172 and elsewhere: Please when you cite a species for the first time in a manuscript provide the full taxonomic name, which include Genus, species name and author(s).

L. 196: see major comments 3.

L. 202-204: Similar thing has been said by Matsuzaki et al. (2016, Mar Micro) also please check it.

L. 211: How is the water depths influencing it? It may be good to also consider it.

L. 218: Silt percentage mean grain size? if so it may be better to use the term grain size.

L. 222-224: Matsuzaki et al. (2019) also showed that higher diversity is reached during interglacial period in the East China Sea over the last 400 000 years. It is supporting your idea.

L. 230-232: See major comment 2.

L. 236-239: What it is written here is of interest however if the grain size affect the diversity as it is written here, it means that it is likely that the dissolution is affecting the assemblages, with coarser grain sizes causing higher dissolution, which may lead the complete disparition of radiolarians having a weaker Si02 skeletons. Thus I also suggest to consider dissolution effect.

L. 255-256: I suggest to check Matsuzaki et al., in press. for Pterocorys % as they published new living records in the Kuroshio Area (Kyushu Pale-Ridge):

Matsuzaki, K. M., Itaki, T. and Sugisaki, S., in press: Polycystine radiolarians vertical distribution in the subtropical Northwest Pacific during Spring 2015 (KS15-4). Paleontological Research. 10.2517/2019PR019

L. 269-273: See major comment 3.

L. 281-287: See major comment 3.

Taxonomy:

There are some important error in particular S. resurgens-> S. biconcavus. Both species clearly lives in different habitat so I think that a careful check should be done on counting Spongodiscus.

A: This is not a typical D. profunda but more Dictyocoryne bandaicum (Harting) See Matsuzaki et al. (2015 Marine Micropaleontology).
E: This is definitely not S. resurgens. This is Spongodiscus biconcavus Haeckel. The very opaque and thick center with the presence of a pylome at the periphery clearly indicate it. See Matsuzaki et al. (2016).
G-H: Good, but I will rather say T. octacantha Muller group as there is a high variability.
K: This is wrong. This is more Flustrella polygonia (Popofsky)
See: Matsuzaki, K. M., Suzuki, N., and Nishi, H., 2015, Middle to Upper Pleistocene Polycystine Radiolarians from Hole 902-C9001C, Northwestern Pacific: Paleontological Research, v. 19, no. s1, p. 1-77.
O: This is wrong. The pores are to big and the shell to rounded for be a C.Huxleyi. I rather recommend to not name this species ore use sp.
P-Q: This is Pseudocubus obeliscus Haeckel.


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: RADIOLARIAN ASSEMBLAGES IN THE SHELF AREA OF THE EAST CHINA SEA AND YELLOW SEA AND THEIR ECOLOGICAL INDICATION OF THE KUROSHIO CURRENT DERIVATIVE BRANCHES
Review round: 2
Reviewer: 1

Output:
Basic reporting: English: Much improved on the original version & nothing really difficult to follow.  I have made some comments in the attached annotated PDF.  I note the enhanced explanations.

References: Appropriate & sufficient.

Article Layout:  Much improved & now suitable for publication.

Tables & Figures: Much improved & now suitable for publication.

Overall:  Self-contained.
Experimental design: Journal Fit:  Within PeerJ Aims & Scope.

Investigation: Good

Methods:  The inclusion of the authors' raw data has enabled me to use open-access software to confirm their RDA results as well as their cluster analysis & detrended CA.
Validity of the findings: Data:
There is now enough raw data to allow replication so I have been able to confirm the authors' results.

Conclusions:
The authors' previous wording which frequently suggested correlation meant causation has been amended.
Additional comments: This version of the paper is a great improvement on the first.  The only criticism I have is that I still feel rather too many statistical tests have been applied.  For example, I am not sure that SIMPER provides any more information than could have been deduced by visual examination of the census data.

Note:  Line 31: Key words omitted – were lines 32-33 in previous version.


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: RADIOLARIAN ASSEMBLAGES IN THE SHELF AREA OF THE EAST CHINA SEA AND YELLOW SEA AND THEIR ECOLOGICAL INDICATION OF THE KUROSHIO CURRENT DERIVATIVE BRANCHES
Review round: 2
Reviewer: 2

Output:
Basic reporting: The manuscript is clear and well-written. The cited literature is sufficient, providing us a good background about the research context. The hypothesis and the data presented here are consistent. To summarize the present manuscript is in a good shape.
Experimental design: The manuscript showed new original data and the method follow the international standards and is well explained. The research is also relevant and have a clear purpose well defined. There are no issues in the design of the research.
Validity of the findings: The finding presented here are relevant and allow the micropaleontological community to have a better understanding of a particular siliceous microfossil group in the East China Sea and the Yellow Sea, which can help to reconstruct hydrography of the past. The used robust statistics and thus it is looking good.
Additional comments: The data is of interest and allow us to have a better understanding of key parameters constraining the distribution and diversity of Radiolarians. The authors also stressed well the importance of not only the Kuroshio Current but also the importance of the Yangtze river discharges of fresh water in the regional ecosystem. Therefore, the authors did an excellent job and the manuscript is in a good shape and I think it is ready for publications.

I have few very minor comments/advices, which may be considered before sending the proofs. They are listed below:

L. 166: Mueller-> Müller
L. 203: adaption-> adaptation
L. 209: According to figure 7, I am not sure that Z. piscicaudatus, E. furcata… are related to lower SSS. They are related to High SST.  There is a bit of over interpretation. I will suggest to delete « lower SSS » .
L. 211: Same than above. I think that there is a bit of over interpretation in saying that T. octacantha fit with lower SST. However higher SSS yes. So I suggest to delete « lower SST » .
L. 241-243: What you wrote is good, but because it seems that there is a latitudinal changes in SST and SSS. So how about the possible effect of solar insolation? You may not need to address it in this MS, but may be good for you to keep it in mind for further studies.
L.276: Matsuzaki, Itaki, Sugisaki (2019)->Matsuzaki, Itaki, Sugisaki (2020)
L. 300-301: I agree what you say, it is true if you just consider the tropical marginal seas. However, if you looked at the entire N. Pacific, it seems that there is a threshold value of about 15℃. This means that Tetrapyle spp. is as you say highly resistant to SST variation, but cannot survive to SST lower than about 15 ℃. (Matsuzaki and Itaki, 2017)


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: DEVELOPMENT OF A NONINVASIVE PHOTOGRAPH-BASED METHOD FOR THE EVALUATION OF BODY CONDITION IN FREE-RANGING BROWN BEARS
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: I only have minor revisions to suggest- great work with this paper! It provides a novel tool that could have broad application the field. See specific comments below:

Line 52-53: Is it fat reserves that allow males to gain greater access to females, or overall body mass/ size?

Line 60 and 85: rephrase “capture surveys” to something like “capture operations”

Line 71: Brown bears are omnivores

General comment: Please define your use of “body condition” in the introduction. It is unclear if you are referring to % body fat or overall body size/mass. It becomes clearer later in the paper, but it would be beneficial to the reader to define this up front.

Lines 102-104: Consider rephrasing to: During 1998–2017, we collected body weights and
morphometrics from brown bears captured for research purposes, killed for nuisance control, or harvested from the peninsula, including the towns of Shari and Rausu (Fig. 1).

Line111-112: remove “near the tip of the peninsula” since you have a figure showing this

Line 132: rephrase to “were obtained from bears killed for nuisance control or from harvest”

Lines 154-156: Please include a justification for why you separated subadult and adult males and females into these categories. Why did you define female maturity as 5 and male as 8?

Line 377: hyphenate “higher energy”

Line 391: or bear species!

Line 402: The following could be an interesting comparison if you want to include a more recent citation for Alaska:
Hilderbrand, G. V., Gustine, D. D., Mangipane, B. A., Joly, K., Leacock, W., Mangipane, L. S., ... & Cambier, T. (2018). Body size and lean mass of brown bears across and within four diverse ecosystems. Journal of Zoology, 305(1), 53-62.


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: DEVELOPMENT OF A NONINVASIVE PHOTOGRAPH-BASED METHOD FOR THE EVALUATION OF BODY CONDITION IN FREE-RANGING BROWN BEARS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The language was clear and professional throughout.  I suggest using additional descriptive terms in addition to "measures" throughout the paper, as many times I did not understand which type of "measures" you were referring to.  For example,

Your abstract needs more detail, specifically in regards to how you defined BCI.  It wasn't into very far into the paper that the BCI method was explained.   The statement in line 43 (short intervals over long periods of time) is confusing, and thus defining what short/long mean by example would strengthen this concept.

I appreciate the thorough review of body condition assessment methods in the Introduction.  Adding the use of ultrasound measures of subcutaneous fat, as in Morfeld et al. 2014 for elephants, would strengthen this section.  More general background on the wide use of body condition scoring in domestic species would be helpful (dogs, cats, etc.), as well as pigs, cattle, horses.  By including these species, this strengthens the rationale of applying similar techniques to wildlife species.

Line 85 - more information why capture surveys are not suitable for ongoing body condition assessments.  The term "capture surveys" is not previously introduced, which could be confusing to some readers.

The most significant challenge and confusion was the strong emphasis on correlation to BCI, but the BCI methods were not introduced until line 88, which is critical component to your paper.  You should spend time explaining what this method was, citation, etc.   It is very unclear as is.

Line 92 - briefly explain what "candidate methods" means.

The tables are overall very well done, with raw data submitted. However, I could not open the Supplemental files with the eps file types.
Experimental design: Overall, the design is suitable, but it did take several reads to understand the three small studies within the larger study.  It would be best to state the overall goal first, and then indicate the necessary steps to get there.

Line 105:  Unclear why you can determine age by teeth of some but not all of your study subjects.

The study area was nicely described.  There is information on measurements in this section that should be moved, as it is not related to "study area" as the section states.  (lines 117-121).  Keeping the field permits in this section is good, but the animal use permit information could be moved to the animal/subject sections.

Line 141.  How are the bears captured more than once, if most were killed for nuisance control/hunting as stated in line 132.  It would be good to include the sample size of killed versus multiple measures in this section.

Bear capture and measurements section- include reference to the appropriate table/figure for this data.

BCI of killed or captured bears:  The BCI methods should be explained more thoroughly.  What did Cattet al al. find?  What is the typical range of BCI?  Was this developed for males, females?  Please provide a review of this method.

Statistics.  Having a separate statistics section would be useful, or at least define the statistics within each section.  It gets confusing and difficult to read with statistical methods throughout the methods and not in a separate section or at least set apart  within each section.

"Shooting and filtering of photographs".  Replace the word "shooting" to something more professional (obtaining, etc.).

Lines 190-193.  The supplemental file has Bear Posture,  Body Arch (A) as either a score option of 1 or 3 (option 2 is blank), but the file with the photos/examples have only Score examples of 1 or 2.  Is this suppose to be a Score of 3?  Or why is the table "blank" for Score 2?

Results. It would be nice to see a resulting table of bears representing the different BCI categories with photos.  It is still confusing to met how the BCI index works, as the table gives negative and positive values. Again, more information on this would be extremely valuable.

Discussion is very well written and addresses the significant findings of the study.
Validity of the findings: The study results are very valuable and I commend the researchers for their thorough efforts on this study.   Overall, the methods and results get confusing to read, but I think separating out sections more thoroughly/accurately, as well as including a separate "Statistical Methods" section would be very helpful.

Again, explain the BCI you are utilizing throughout this paper as the gold standard for your validation.  Without that level of information, it is difficult to interpret the results with clear context/meaning.

Wonderful subject, creative, and thoroughly executed, but clearer writing would help transform your robust study into more user friend action.
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: JATROPHA CURCAS ORTHOLOG OF TOMATO MADS-BOX GENE 6 (JCTM6) PROMOTER EXHIBITS FLORAL-SPECIFIC ACTIVITY IN ARABIDOPSIS THALIANA
Review round: 1
Reviewer: 1

Output:
Basic reporting: Physic nut (Jatropha curcas L.) is an important biodiesel resource, although its low seed yield significantly limits its potential. The authors of this study sought to identify a Jatropha curcas promoter that would likely be involved in flower yield improvement, it’s an interesting project.
Experimental design: The experimental design is good, but there are still some experiments and results should be provided.
Validity of the findings: This study isolate a JcTM6 promoter in Jatropha curcas, which might be useful for the jatropha breeding in the furture studies.
Additional comments: However, there are still some comments for the authors to substantively revise the manuscript.

1. One of the major issue is the approach adopted to analyze the role of JcTM6 promoter in Arabidopsis. The authors expressed JcTM6 promoter and introduce this construct into Wild-type Arabidopsis plants. Then all the comparison made between wild-type Arabidopsis plants and wild-type plants that over expressed JcTM6 promoter. As we all know, the Arabidopsis thaliana is a model plant, and a frequent but inappropriate or inconclusive approach to isolate the function of the heterologous gene.

2. The function of JcTM6 is not clarified in this study. Only the expression pattern of JcTM6 is not enough to illustrate its roles.

3. Based on the manuscript, the fragment of the JcTM6 promoter is about 1.8-kb, from–1717 to +103 bp. The rough result is that why only the 842-bp fragment of the JcTM6 promoter (–1,717 to –876 bp) was deleted to identify the function of JcTM6. The author shows that this deleted region contained one of the two CArG box motifs, but what about the other one. I noticed the Arabidopsis AP3 promoter contains three CArG boxes with different functions (Line 215-218). Generally, a series of deletions of the JcTM6 promoter should be generated to analyze the regulatory effect of different regions of the promoter, and then the vital region could be accurately confirmed. I think more interesting and useful results would be obtained.

4. I noticed that JcTM6 promoter was used to drive the AtIPT4 gene. I think the Figure 6 is rough to present the function of JcTM6 promoter. It’s not clear that the different morphological results were caused by the JcTM6 or AtIPT4 in Arabidopsis thaliana. Moreover, the sole morphological results provided do not exclude a possible silencing of the endogenous transcript. So, I suggest that, at least, the cytokinin contents must be investigated to confirm the results, and not only the morphological observations. The characters of floral organs and the expression abundance of the genes associated with cytokinin synthesis and transduction pathways should also be observed between the wild type and transgenic plants.

5. I did not check whether the references were all mentioned.

I would suggest the authors should make substantial and in-depth revisions to the manuscript. The conclusions in the manuscript are based on more data than the data presented in the current manuscript, and then the authors should restate their discussion and conclusions.


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: JATROPHA CURCAS ORTHOLOG OF TOMATO MADS-BOX GENE 6 (JCTM6) PROMOTER EXHIBITS FLORAL-SPECIFIC ACTIVITY IN ARABIDOPSIS THALIANA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article untitled ‘Jatropha curcas ortholog of tomato MADS-box gene 6 (JcTM6) promoter exhibits floral-specific activity in Arabidopsis thaliana’ is well written and clear. English is correct and easy to understand. I have only a small correction on line 190 ‘TM6 functions as a class B gene that play an essential role in stamen development’ and on line 193 ‘Both genes are predominantly …..’

The literature references are adequate. Nevertheless, there is a typing mistake on line 145 and 359 ‘Meyerowitz’ instead of ‘Meyerowltzt’

The context is clearly explained in the Introduction. However, I suggest you add some information about the flowering and reproduction of Jatropha (lined 60-61). For example, mention that Jatropha is a monoecious plant species. It would help the reader to understand the importance of male to female flower ratio. It would also clearly state why you investigate the gene expression in male and female flowers.

The structure of the article is clear and the figures and tables are clear and adequate. The raw data are shared in the supplemental data
Experimental design: The proposed article corresponds to the scopes of the journal. The research questions are well defined in the Introduction. The experimental design is relevant to answer the research questions. The methods are clearly described but the number of replicates is sometimes missing. Please provide the number of biological replicates and repetitions that were used for the qRT-PCR analysis (line 104) and the GUS staining assays (line 130).

Regarding the deletion analysis, it is not clearly stated why you choose to remove this part of the promoter and not another neither why you analyze only one deletion and not several to understand more clearly the role of the different parts of the promoter. Please justify your strategy either in the 'material and methods' or the 'result' sections.
Validity of the findings: The results are well presented and raw data are available.  The conclusions are well stated and answer the research question.
Regarding the phenotype of the JcTM6::AtIPT4 transgenic Arabidopsis flowers, were all floral organs affected in the same way? Are the stamens and petals more affected than the other floral organs? Indeed, you show that the promoter is mainly active in the stamens and that the gene expression is higher in petals and stamens. Do you have some numerical data for flower comparison? It would help to be more precise on the observed phenotype. On the same way, you conclude from your results that the JcTM6 promoter is a flower-specific promoter. However, it is not active in all floral organ. Could we consider that it is more a stamen-specific promoter?
Additional comments: no additional 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: JATROPHA CURCAS ORTHOLOG OF TOMATO MADS-BOX GENE 6 (JCTM6) PROMOTER EXHIBITS FLORAL-SPECIFIC ACTIVITY IN ARABIDOPSIS THALIANA
Review round: 2
Reviewer: 1

Output:
Basic reporting: all my previous comments and requirements were answered in the new version of the manuscript
Experimental design: all my previous comments and requirements were answered in the new version of the manuscript
Validity of the findings: all my previous comments and requirements were answered in the new version of the manuscript
Additional comments: all my previous comments and requirements were answered in the new version of the manuscript