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: IDENTIFICATION AND MOLECULAR CHARACTERIZATION OF THE ALTERNATIVE SPLICED VARIANTS OF BETA CARBONIC ANHYDRASE 1 (ΒCA1) FROM ARABIDOPSIS THALIANA
Review round: 1
Reviewer: 2

Output:
Basic reporting: Although the manuscript flows well, a significant amount of the text has English grammar and sentence structure mistakes. I recommend the authors use an English editorial service to help refine the text. Here are some (not all) examples where the text can be edited:
1.	Please be careful of using italics (βCA1 gene) or not (βCA1 protein).
2.	Line 32 – Please remove, “study of…” so the line reads, “…we focused on the characterization of…”
3.	Line 34 – “variant” should be “variants”
4.	Lines 34-36 – This sentence should be reworded to, “The results showed that the spliced variants of βCA1 possessed different subcellular and tissue distributions and responded differently to environmental stimuli.”
5.	Line 52 – Please remove “the” so the line reads, “…gas and ion exchange…”
6.	Line 55 – Please add, “and” so the line reads, “…and lipid and fatty…”
7.	Line 58 – Please change to, “…based on their conserved nucleotide sequences,”
8.	Line 62 – Please remove “And” so the sentence starts as, “A similar number of genes…”
9.	Lines 65-67 – Please re-word as, “However, there are over 25 genes coding for CA in soybean due to a past genome duplication (DiMario et al., 2017).”
10.	Line 89 – Please remove “firstly”
11.	Line 101 – Please modify “μmol•m-2•s-1” to “μmol photons m-2 s-1” with the appropriate superscripts.
12.	Line 107 – Please remove “kept”
13.	Lines 126-127 – Please reword as, “Coding sequences (CDS) and corresponding genomic DNA (gDNA) sequences of the…”
14.	Line 199 – Please change “N-terminal” to “N-terminus”
15.	Line 200-201 – Please reword as “…lacking the chloroplast transit peptide at the N-terminus and 11 amino acids at the C-terminus, respectively.”
16.	Lines 201-202 – Please reword as, “Moreover, the shortest βCA1.4 variant was truncated at both ends of the protein.”
17.	Lines 203-204 – Please reword as, “…the expression pattern of each variant was analyzed.”
18.	Lines 210-213 – Please reword as, “On the contrary, expression of βCA1.2 was higher in flower and fruit tissues than in leaves and inflorescences. The expression levels of βCA1.3 were weaker than the expression levels of βCA1.4, and βCA1.3 transcripts were rarely detected in flowers.”
19.	Line 216 – Please change “code” to “codon”
20.	Line 221 – Please change “it’s” to “it is”
21.	Line 226 – Please change “localization” to “locations”
22.	Line 228 – Please change to, “In one-week-old seedings…”
23.	Line 235 – Please change to, “In the root tips, a strong fluorescent signal was detected only for βCA1.4, whereas…”
24.	Line 242 – Please reword as, “The CA1 family is…”
25.	Line 244 – Please remove “hormone”
26.	Line 245 – Please change “stress was…” to “stresses were…”
27.   Line 284 - Please change "frechuntely" to "frequently".
28.	Line 291 – Please add “the” to the beginning of the sentence. Also, please remove “in” so the next sentence reads, “Both mammalian and plant cells…”
29.	The wording/English of the discussion section can use some refining as well.

The introduction provides a nice background on carbonic anhydrases (CA) and pertinent CA references are sighted for the most part. There are some issues:
1. Should the reference section be organized in alphabetical order?
2. Lines 242-243 - DiMario et al., (2017) is a review article. Should the original research articles be referenced here?
3. Lines 378-379 - The interaction between PIPs and βCA4 in Arabidopsis thaliana has already been confirmed (Wang et al., 2016. The Plant Cell. 28: 568-582).

The article is structured well. However, the figures could be of better quality (higher resolution.) Also, the authors introduce new data in the discussion section (Fig. S5; line 334). It seems that introducing new data in the discussion section is not usually allowed, but I will leave this up to the authors to decide to move this to the results section or not.
Experimental design: The research is a good fit with the Aims and Scope of the journal.

The authors do a good job of identifying a knowledge gap in the plant CA field and their research does address this gap.

There are some issues with the experimental design and how the methods are written:
1. Lines 98-99 - The βCA2 mutant line does not seem to be used in this study. Additionally, Huang et al. (2017) used a βca1βca2βca4 triple mutant and did not characterize the βca1 T-DNA single mutant used in this study.
2. Additionally, with the known problems of secondary mutations with T-DNA mutants, backcrossing or at least complementation lines are necessary controls for growth experiments. Did the authors perform backcrosses on the βca1 T-DNA line? Is it possible to generate complementation lines by inserting a functional AtβCA1 gene back into the βca1 T-DNA line?
3. Line 150 - If reporting in RPM, the centrifuge and rotor information must be provided, too. Or, reporting the centrifuge step in g is an option.
4. Figure 1C - For expression semi-quantification using RT-PCR, it is important to standardize the primer sets where the primer pairs amplify the same size amplicons and are located in similar regions of genes (as 3' ends of transcripts are more easily reverse transcribed versus 5' ends in some cases.) The different locations of the primer sets along the βCA1 gene could not be helped as the authors had no choice there, but it is possible to standardize the size of the different PCR products. I just wonder if amplicon size had an impact on the results of expression strength.
5. For Figure S3 - I may have misunderstood this experimental setup. I do not understand how you can differentiate between the different βCA1 protein variants when using 1.5 kb promoter regions upstream of the different transcription start sites of the variants. These different 1.5 kb promoter regions have significant overlap with one another at the 5' regions, particularly for βCA1.1, βCA1.2, and βCA1.4. How can you be certain that you are not picking up the correct βCA1 variant?
6. Figure 3B - A minor question. Are the wild-type (WT) and βca1 mutant seedlings growing on the same plate, or are they growing on their own independent plates? In the past, have groups tried to grow different genetic lines on the same large agar plates to reduce variability?

Overall, the methods section is written well and descriptively.
Validity of the findings: The GFP and βCA1 protein interaction datasets are very interesting and the authors overall provide an interesting story with their manuscript.

There are some issues with other datasets/conclusions in the manuscript:
1. I am speculating here, but I question the validity of Figure 1D in relation to Figure 1A - According to the alignment in Figure 1A, βCA1.1 and βCA1.2 should have the same molecular weights (and isoelectric points since they are the same sequence) once the chloroplast transit peptide (cTP) has been cleaved from βCA1.2, yet there are two distinct band sizes for βCA1.1 and βCA1.2. The same can be said for βCA1.3 and βCA1.4 as these two proteins should also run on top of each other in the protein gel. I also question the identification of the chloroplast transit peptide in Figure 1A. Running the βCA1 peptide sequence through ChloroP - the chloroplast transit peptide prediction program (http://www.cbs.dtu.dk/services/ChloroP/), the predicted cleavage point is around ALA104 (which has the highest CS-score - most likely residue to be the cleavage point of the cTP). An alanine as the cleavage residue makes more sense than the GLU-MET region indicated as the cleavage point for the cTP. If ALA104 is the true cleavage site of the cTP, then the mature βCA1.2 and βCA1.3 proteins with cleaved cTPs should actually be smaller than than βCA1.1 and βCA1.4.
2. As mentioned above, there are known issues with Arabidopsis T-DNA mutant lines. If the βca1 T-DNA line has not been backcrossed (which was not stated by the authors), then a couple independent complementation lines with a functional βCA1 gene inserted back into the βca1 line is a necessary control for the heat stress growth experiments.
3. Again, the GFP localization data are very nice and very interesting. However, with lines 232-233 and lines 324-325 - I do not think you can say βCA1.4 is localized to both the cytosol and plasma membrane. I agree βCA1.4 is likely in the cytosol, but you will need further experimental proof to say that βCA1.4 is also in the plasma membrane. Due to the central vacuole pushing organelles and the cytosol outward toward the plasma membrane, a cytosol fluorescent signal can look like a plasma membrane signal at times.
4. Lines 325-326 - Are there any references for C-terminal regions being cTPs? I thought cTPs were strictly at the N-termini of proteins?
5. In the Discussion section, it would be nice to point out how important it was to find that alternatively spliced variants are resulting in different βCA1 proteins that have different subcellular locations. This is important because: 1) CA proteins may be more redundant within subcellular locations (i.e. there may be more CAs in a subcellular location that can compensate for loss of CA activity due to mutation) and 2) this may bolster the potential physiological roles of CA.
Additional comments: Again, the GFP localization and βCA1 protein interaction datasets are very nice and interesting.


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: IDENTIFICATION AND MOLECULAR CHARACTERIZATION OF THE ALTERNATIVE SPLICED VARIANTS OF BETA CARBONIC ANHYDRASE 1 (ΒCA1) FROM ARABIDOPSIS THALIANA
Review round: 1
Reviewer: 3

Output:
Basic reporting: Manuscript by Shen et al. “Identification and molecular characterization of the alternative spliced variants of beta carbonic anhydrase 1 (βCA1) from Arabidopsis thaliana” describes the study of an important problem of the functioning of plant carbonic anhydrases, whose functions in higher plants are still largely unknown. The authors obtained valuable data on the characteristics of the most abundant in plant leaves carbonic anhydrase, βCA1. The presence of enzyme splicing, and in particular of carbonic anhydrases, reveals new features of the metabolism of living organisms. The presented study of this question for an enzyme such as βCA, whose functions remain mysterious, makes a great contribution to our understanding of these functions.
The structure of the manuscript is standard and contains all the necessary parts. Further analysis of the text will be given separately by sections. However, first about the language. English is grammatically correct, but very difficult to read and understand, the authors need to improve it for clarity. Some obvious errors will be noted further.
Abstract fully reflects the content of the work.
Introduction contains the data necessary to justify the undertaken work, and the references reflect the problems that arise. However, very little space is given directly to the problem of βCA1 functioning in plants. Surprisingly, the authors did not mention a work published as early as 2107 (Rudenko et al. Biochemistry (Moscow), 2017, Vol. 82, No. 9, pp. 1025 1035). In this work, the dependence of the spliced variables of βCA1 on light intensity and photoperiod was investigated, and the latter is important for understanding the results of this manuscript. In that work the expressions levels of two spliced variants of βCA1 were studied, and it was sown that they were different at short (8 h day/16 h night) and long (16 h day/8 h night) photoperiods, the last was used in authors’ study (line 102 in the manuscript).
Materials and methods are described in sufficient detail to be able to reproduce the experiments of the authors. However, there are a number of observations.
Line 119. Tablet S1?? Check it.
Line 124. Replace word ‘seed’ to more appropriate one. The same in the line 189 in Results.
Lines 151-155. The description of immunoblotting is required to be more in detail! Especially about the reagents used.
Experimental design: Materials and methods are described in sufficient detail to be able to reproduce the experiments of the authors. However, there are a number of observations.
Line 119. Tablet S1?? Check it.
Line 124. Replace word ‘seed’ to more appropriate one. The same in the line 189 in Results.
Lines 151-155. The description of immunoblotting is required to be more in detail! Especially about the reagents used.
Validity of the findings: Results.  The description of the results obtained is enough clear, but it is desirable that the most important results are more clearly indicated.
Lines 204-206 repeat lines 116-118 in the Methods. The approach would be preferably to present in more detail in the Results.
Line 209. It is necessary to describe how the material from the "inflorescence" was prepared.
Line 220. The word" while" distorts the meaning of the sentence.
Line 245. ‘βCA1.2+βCA1.3’ should be replaced with ‘βCA1.3+βCA1.4’!!
	Since co-immunoprecipitation can be non-specific, the data described in the relevant part seem questionable. Such concern confirms by the fact that co-immunoprecipitation for βCA1. 4 was detected with photosystem-bound proteins (line 281), although “no visible signal can be detected in chloroplasts from either stomata or leaf protoplasts” (line 234).
Line 284. "frechuntely" or "frequently"?
Discussion.
This part of manuscript is rather adequately reflected the results obtained. However, some discussion about physiological functions of spliced variants of βCA1 in the different locations is necessary, as it was recommended also for Introduction.
It may be noted such important conclusions as ‘that the individual spliced variant of βCA1 may function in vivo’ (line 309). However, in some places the clarification of authors’ statements is required.
Lines 317 - 323. The authors ' reasons for explaining the difference between their results and the data by Hu et al. (2015) seem rather light and contradictory. A more detailed discussion is needed.
Lines 354 – 355. “In the present study, βCA1.1 and βCA1.4 were found induced by salt and heat 355 stresses, whereas βCA1.2 and βCA1.3 were significantly repressed.’ However, this conclusion was made in Results only as assumption!!
Line 359. ‘βca2’ in italic. Possibly, this is incorrect.
Lines 377 - 378. βCA4.1 should be instead of βCA1.4.
The figures and tables in the main text are suitable.
Very serious. The legends to Tables and figures are absent for supplementary data.
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: IDENTIFICATION AND MOLECULAR CHARACTERIZATION OF THE ALTERNATIVE SPLICED VARIANTS OF BETA CARBONIC ANHYDRASE 1 (ΒCA1) FROM ARABIDOPSIS THALIANA
Review round: 2
Reviewer: 1

Output:
Basic reporting: Overall, the paper flows well. There are only a few minor typos:
1.	Line 28 – in the abstract, “oxide” should be “dioxide”.
2.	Line 48 – There should be a space between “tissues” and “across”.
3.	Line 98 – in the methods, “soli” should be “soil”.
4.	Line 192 – in the results, “an” should be deleted so the line reads, “…alternative 5’ or 3’ splice site.”
5.	Line 214 – in the results, “I,” should be deleted.
6.	Line 244 – in the results, there should be a space between “the” and “heat”.
7.	Line 283 – in the discussion, “various” is used twice in this sentence. Maybe substitute one of the “various” words with “many”?
8.	Line 288 – in the discussion, should “redundant” be replaced with “abundant”?

The introduction provides a nice background on carbonic anhydrases (CA) and the pertinent CA references are cited.

The article is structured well. Some figures may need to be of better quality; however, this may be from my PDF viewer. I leave this up to the discretion of the authors and editor.
Experimental design: The research is a good fit with the Aims and Scope of the journal.

The authors do a good job of identifying a knowledge gap in the plant CA field and their research does address this gap.

Overall, the methods section is descriptive and well-written.
Validity of the findings: The GFP and βCA1 protein interaction datasets are very interesting.

I am still concerned that the protein alignments of Figure 1B indicate that the mature βCA1.1 and βCA1.2 proteins and the mature βCA1.3 and βCA1.4 proteins are the same size (and have the same isoelectric points due to identical peptide content), yet they run at two different protein sizes on their respective gels. However, this does not take away from the main points that are being made by this study.
Additional comments: The authors did a fairly good job of responding to the manuscript’s critiques and made the corresponding changes that were needed.

Again, the GFP localization and βCA1 protein interaction datasets are very nice and interesting.


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: INTEGRATED TRANSCRIPTOMIC AND PROTEOMIC ANALYSIS OF TRITIPYRUM PROVIDES INSIGHTS INTO THE MOLECULAR BASIS OF SALT TOLERANCE
Review round: 1
Reviewer: 1

Output:
Basic reporting: It sounds relevant.
Experimental design: Moderately okay.
Validity of the findings: Considerable.
Additional comments: The manuscript reveals differential tolerance to salt stress through proteomics analysis supported by the downstream qPCR experiments. The work is a straightforward proteomics analysis, which was further annotated based on the existing database search. Although the manuscript may advance our understanding of salt tolerance in Tritipyrum, I would suggest some improvements to be done before considering for publication.
Line 94: How do you know that these genotypes are having contrasting tolerance to salt stress? Any reference or preliminary experiments on that?
Line 104: Although the sensitivity to NaCl depends on species/cultivars, 250 mM NaCl is too high. Why did you choose this concentration for inducing salt stress? How about the pH of the solution culture?
Line 118: Please briefly write the protein extraction method.
Line 138: List the names of the genes studied for qRT-PCR.


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

Input:
Title: INTEGRATED TRANSCRIPTOMIC AND PROTEOMIC ANALYSIS OF TRITIPYRUM PROVIDES INSIGHTS INTO THE MOLECULAR BASIS OF SALT TOLERANCE
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript by Yang R and colleagues delineates the molecular understanding of salt tolerance in Wheat (Triticum aestivum) utilizing both transcriptomic and proteomic analysis. The authors utilized salt-tolerant and salt-sensitive wheat to find differentially expressed genes and proteins to address the molecular pathways and processes important for the salt-tolerant phenotype in wheat. I found this study to be interesting, well-crafted, and insightful.
Experimental design: 1.	qPCR validations were carried out using the same samples used for proteomic analysis. I would recommend using separate samples for the validation process to ensure the reproducibility of the findings
Validity of the findings: 2.	The authors mentioned differentially expressed proteins in other species like barley, rice, sweet potatoes (in the introduction). It would be interesting to know the common DIPs among different species to single out the most prominent molecular pathways/processed involved in salt tolerance.
3.	It would be helpful to dissect the role of some of the differentially expressed genes/proteins experimentally using genetic knockdown/knockout or overexpression experiments.
Additional comments: 1.	I would suggest elaborating figure legends to ensure better readability.


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: INTEGRATED TRANSCRIPTOMIC AND PROTEOMIC ANALYSIS OF TRITIPYRUM PROVIDES INSIGHTS INTO THE MOLECULAR BASIS OF SALT TOLERANCE
Review round: 2
Reviewer: 1

Output:
Basic reporting: May be considered for publication.
Experimental design: May be considered for publication.
Validity of the findings: May be considered for publication.
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: INTEGRATED TRANSCRIPTOMIC AND PROTEOMIC ANALYSIS OF TRITIPYRUM PROVIDES INSIGHTS INTO THE MOLECULAR BASIS OF SALT TOLERANCE
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors successfully addressed all of my questions and concerns.
Experimental design: No comment
Validity of the findings: No comment
Additional comments: No additional comments


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

Input:
Title: REINVESTIGATING THE PHYLOGENY OF MYRIAPODA WITH MORE EXTENSIVE TAXON SAMPLING AND NOVEL GENETIC PERSPECTIVE
Review round: 1
Reviewer: 1

Output:
Basic reporting: .
Experimental design: .
Validity of the findings: .
Additional comments: Review of submission #64880, by Wang et al., to PeerJ

The submission in review is a very nice, smart and useful paper, easy reading and finely illustrated, that sheds new light on the phylogenetic interrelations between four major classes of Myriapoda, using a rich array of candidate outgroups. I would immediately recommend publication had it not been for a few reproaches, all easy to consider though.

The flaws as I see them are mainly rooted in the authors’ apparent negligence in taxonomy. Why term the CLASSES Chilopoda, Diplopoda, Symphyla, and Pauropoda either as “subfamilies” (a distinct taxonomic category, albeit applied wrong) or “subgroups” (not wrong, but inexact)?
It would also seem advisable to show the sampling set (Table 1) in a clearer taxonomic context (e.g. structured as per order). Thus, there are 16 orders (taxonomic categories!) among extant Diplopoda, and five in Recent Chilopoda, but whereas your taxon listing includes representatives of all five orders of Chilopoda, that of Diplopoda contains members of only nine, i.e. far from complete and thus not too representative (especially so as regards blind taxa).

Indeed, among Diplopoda there are several ORIGINALLY and TOTALLY blind orders such as Polydesmida or Platydesmida, representatives of both of which are listed in Table 1. The same concerns the entire order Geophilomorpha or the family Cryptopidae (order Scolopendromorpha) of the class Chilopoda. What about their LIT genes versus those of the “eyed” orders? It has been very clever for the authors to consider the soil as a major environmental factor to have affected the evolution of the blind and mostly soil-dwelling Symphyla and Pauropoda which are reconfirmed as being particularly close phylogenetically, but, as noted above, several orders (the Polydesmida is the largest and most diverse amongs all Diplopoda!) or families (taxa!) of Myriapoda, both soil-dwelling and epigean, are likewise blind and thus requiring special attention (or at least mention if not a brief discussion) as regards the LIT data.

A single typo spotted:
Line 320, not Scoropendra but Scolopendra

Only two small lapses noted, as follows:
Line 438, italicize “Koenig” as well, since the Bonn Museum is named after Alexander Koenig
Line 440, it must read “Bonner Zentrum für Molekulare Biodiversitätsforschung (ZMFK)” (NB: Two Umlaut as diacritics)!

As a verdict, I believe the paper is outstanding and definitely merits publication, yet this being possible only upon MINOR revision. I do not think another round of peer reviewing is necessary.

I do not mind if my name as that of a reviewer is revealed to the authors.

Moscow, September 8th, 2021
Sergei Golovatch


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: REINVESTIGATING THE PHYLOGENY OF MYRIAPODA WITH MORE EXTENSIVE TAXON SAMPLING AND NOVEL GENETIC PERSPECTIVE
Review round: 1
Reviewer: 2

Output:
Basic reporting: This is a neat paper that reconstructed the phylogeny of Myriapoda based on transcriptomic data with high support values. However, some major weaknesses made me reject this manuscript.

1. Introduction of the background is insufficient. For example, the authors should explain the difference of habitat between Pauropoda + Symphyla and Chilopoda + Diplopoda in detail.

2. Citations need to be modified. For instance, the citations of the sentence in lines 44-46 were confused.

3. Some expressions need to be more specific. For example, in lines 33-34, the authors said ‘Myriapoda…including millipedes, centipedes, and others’. Myriapoda is the topic of this manuscript and there are only four classes in Myriapoda. Why not introduce them all?
In lines 34-35, the description of the diagnostic characteristic of Myriapoda is ambiguous. In accordance with this state, is a spider with 8 legs a myriapod?
In line 39, the authors said ‘the described extant species of all four subgroups are abundant’. It’s wrong. Actually, only Chilopoda and Diplopoda are species-rich, and Pauropoda and Symphyla are much less speciose (Szucsich et al. 2020).

3. Some terms were erroneously used. For instance, “Dignatha” in line 44 should be changed as “Edafopoda” and “Edafopoda” in line 45 should be changed as “Dignatha” (replace these two terms).
The authors regarded the four subgroups of Myriapoda as ‘subfamily’ (in lines 282, 287, 288, 331, 332, 334, 352, 362, 367). This is wrong. The taxonomic category of Diplopoda, Chilopoda, Symphyla and Pauropoda is class rather than subfamily.
In line 140, if the authors used Akaike Information Criterion then the abbreviation should be AIC. AICc stands for corrected Akaike Information Criterion.

4. Sentences in lines 358-359, ‘...instead of just one species in previous studies. This may increase the risk of mispositioning PAU in quartet topology’ is better to changed as ‘...instead of just one species in previous studies which may increase the risk of mispositioning PAU in quartet topology’

5. The word ‘and’ in line 45 was not typed in Times New Roman.

6. The first ‘CHI’ in Supplementary_Figure_1 should be ‘CHE’.
Experimental design: The fatal flaw of this manuscript is in this part. The authors state that the habitat of Pauropoda and Symphyla is soil, and it may impact their visual capabilities. However, actually, all four subgroups of Myriapoda are terrestrial arthropods and inhabiting the soil. Why the influence only occurs in Pauropoda and Symphyla, and disappears in Chilopoda and Diplopoda? Furthermore, even if there is a difference in visual ability between Pauropoda + Symphyla and Chilopoda + Diplopoda, it also could be a consequence of convergent evolution. Therefore, the visual ability couldn’t provide evidence for the monophyly of Pauropoda and Symphyla.
Validity of the findings: no comment.
Additional comments: no comment.


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

Input:
Title: REINVESTIGATING THE PHYLOGENY OF MYRIAPODA WITH MORE EXTENSIVE TAXON SAMPLING AND NOVEL GENETIC PERSPECTIVE
Review round: 1
Reviewer: 3

Output:
Basic reporting: The English language is generally clear, unambiguous and professional. However, I found the following ambiguous or imprecise points, which deserve corrections or clarifications:
- the 4 clades (Chilopoda, Symphyla, Diplopoda, and Pauropoda) are variously called subgroups or subfamilies in different paragraphs of the article; however, they are not "subfamilies" in the current and traditional taxomomy, accordig to established conventions of taxonomic nomenclature;
- lines 44-45: the names Dignatha and Edafopoda are exchanged erroneously;
- line 45: "which strongly contradicted the phylogenetic relationships (sister group of DIP+PAU, named Edafopoda)"; the meaning is unclear. Perhaps the meaning is: "which contradicted the sister-group relationship DIP+PAU (named Edafopoda)".
- "Scolopendra" is sometimes misspelled "Scoropendra"
- line 116: "We confirmed the orthology relationships of the 60 selected taxa". The wording is unclear.
- lines 178-183: brackets and other signs at the end of the lines are excessive
- line 199: "The substitution rate [...] was aligned": the wording should be more precise
- line 238: "in the right clade"; avoid "right/wrong", because the true phylogeny is unknown, and we have only hypotheses;
- Table 1: "Ailas" misspelled?
- Table 2: some abbreviations in the table (e.g. Pau-test) do not correspond to the abbreviations in the legend (AU)
- line 349: "phylogenomic analyses on Myriapoda phylogeny"; wording redundant
- line 388: "intraspecific" perhaps is misspled for "interspecific"

The literature references are sound and adequate. However, I invite the authors to consider the state of knowledge on the ecological and habitat diversity of Chilopoda and Diplopoda, if they want to keep presenting the LIT gene analysis as useful and informative on the phylogeny between the four clades [but see my comments below].

The general structure of the article is standard, but there are many redundant paragraphs that duplicate information. For instance:
- the methods and results are reported already in too much detail in the Introduction;
- the methods are repeated in too much detail in the Result section

The trees in suppl. fig. 2-5 appear without bootstrap values, but the authors wrote (line 269) "negligible support could be obtained from bootstrapping". Authors should show statistical supports for these trees.
Experimental design: The major merit and originality of this study is to have integrated two independent datasets,  previously analysed independently, in a single analysis, so that to increase the taxon sampling.
Validity of the findings: The phylogenetic analysis is well done, sound and rigourous.
Also the LIT gene analysis appears well done, rigorous and very original for the Myriapoda. However, it is not fully clear how the LIT gene analysis can contribute to the general explicit aim of the study (clarify the phylogentic relations among the four clades).
The rationale of employing the LIT gene analysis to add support to the phylogenetic hypothesis should be explained more clearly and more precisely by the Authors.
If, instead, the LIT gene analysis does not bear on the phylogenetic reconstruction, it should be presented not as an additional tool for the assessment of phylogenetic hypotheses, but merely as a complementary, orginal evaluation of the evolution of vision and vision-related genes in the Myriapoda as a whole.
In the present manuscript, the following senteces should be provided with arguments or, alternatively, revised:
- line 23: "provide a new perspective to observe the above-mentioned question, since we also identified the visual genes..."
- line 28: "From [...] the new perspective gained by visual genes, we propose that Symphyla is a sister group of Pauropoda ..."
- line 73: "We attempted to find additional evidence to support PAU+SYM and found
that their common habitat is soil".
- line 369: "The respective grouping of PAU and SYM on this basis could make sense"

Moreover, authors do not present and not discuss the results of the Bayesian analyses. These results should be reported , at least briefly, and the trees provided in the Suppl. Mat. at least.

When describing the phylogenetic results (lines 235 and following), the author describe only the topology obtained from the OCC90 matrix, but they should tell explicitly also that the OCC100 matrix produced a different topology, contraddicting the Edafopoda hypothesis.
Additional comments: Some statements appear partly questionable, or imprecise, or subjective. So, I invite the authors to reconsider them and avoid any statement that sounds subjective or opinion non based on evidence.
In particular:
-    line 34: "The most distinct myriapod characteristic is that their number of legs range from 6 to 750". Actually, it seems subjective. One can say that another character is "the most distinct", e.g., the elongate shape of the body, or the structure of the  mouth parts, or the adaptation to terrestrial environment... Moreover, the range of variation of leg number is very huge, and so hardly "diagnostic" (=distinguishing Myriapopa from all other animals) and other animal groups share similar and partially overlapping numbers of legs (Onychopora, some crustacean groups, ...).
- line 74: ".. PAU+SYM and found that their common habitat is soil". This is also true for most Chilopoda and Diplopoda. Even if the author refer to strict endogeic life (inside the soil, without epigeic activity), they shoud consider that large subclades of Chilopoda and Diplopoda are structly endogeic and blind, like PAU + SYM.
- "Our sampling was designed to maximise the representation of all four myriapod groups" is erroneous, because all available genomic datasets have been used, without any selection, and the new sequenced taxa were not chosen to maximize the representation of the 4 clades (of the 3 taxa, 2 were of the same clade DIP).
- line 354: "The most innovative point of our study was the addition of three...". Actually, the addition of three new transcriptomic datasets is not so crucial for the study, because they are from three species belonging to the two largest clades (Chilopoda and Diplopoda), and in particular to species well nested within the clades (not basally diverging subclades), and not belonging to the focal clade of the study (Pauropoda).
- line 359: "We believe that in molecular studies, the more extensive a taxon sample collection, the
more convincing the phylogeny results". This is well established, by means of many studies. Authors should presnet this statement as an evidence-based knowledge, not as a personal "belief" (opinion).
- line 361: "It seemed as though debates on the interrelationship among the four main Myriapoda subfamilies could never be settled by phylogenomic analyses alone". Why? Phylogenomic analyses by Szucsich et al. and by the Authors provide a robust phylogeny.
- line 386: "could reflect rapid adaptive changes". Why rapid?


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: IDENTIFYING BIOMARKERS FOR EVALUATING WOUND EXTENT AND AGE IN THE CONTUSED MUSCLE OF RATS USING MICROARRAY ANALYSIS: A PILOT STUDY
Review round: 1
Reviewer: 1

Output:
Basic reporting: There are several typo errors, it is recommended that a native English speaker review the manuscript.
The supplemental tables information does not coincide with the text (i.e. page 13, line 276).
It is confusing in the title of the manuscript about the evaluation of the extent of the wounds since the authors only classify the wounds in mild and severe depending on energy applied to the rat´s muscle, and they don´t mention other characteristics of this type of wounds in their model. I think the authors should clarify this point.
I suggest the authors include an English translated version of the Institutional Animal Care and Use Committee.
Figures 2b-i, could be as supplemental figures.
It is not mentioned to what correspond the line colors in figures 3c-e and figures 5c-e. Also, the name of the genes should be mentioned in these figures.
Better legend of figures is required.
Experimental design: The authors should explain how the identification of hub genes distinguish the extent of the injury, and how they are related with the markers found for injury time in mild and severe contusion.
It is not clear the criteria used to select the Rrad, Gpnmb, and Timp1 for RT-qPCR validation. Also, the authors should validate some of the fifteen genes found differentially expressed in supplemental table 1.
They should mention in the text the housekeeping genes and the genes explored in the validation with qRT-PCR. Also, it is missing the primers and probes in Table S1.
Validity of the findings: I think the authors should discuss about the grouping of 1h-M with 3h-M, and 1h-M with 168h-M in figures 3a and 3b.
It would be interesting if authors mention which genes of the 60 most significant found in mild and severe groups are shared between them.
Additional comments: No comments.


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

Input:
Title: IDENTIFYING BIOMARKERS FOR EVALUATING WOUND EXTENT AND AGE IN THE CONTUSED MUSCLE OF RATS USING MICROARRAY ANALYSIS: A PILOT STUDY
Review round: 1
Reviewer: 2

Output:
Basic reporting: .
Experimental design: .
Validity of the findings: .
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: IDENTIFYING BIOMARKERS FOR EVALUATING WOUND EXTENT AND AGE IN THE CONTUSED MUSCLE OF RATS USING MICROARRAY ANALYSIS: A PILOT STUDY
Review round: 1
Reviewer: 3

Output:
Basic reporting: The authors discussed a very important and interesting topic and they included all results relevant to their hypothesis, however, there are some comments on certain parts of the manuscript that need to be modified
Experimental design: The experimental design, although clear, but will be better to show it in a simplified figure
Validity of the findings: the research topic shows novelty. all data have been provided. conclusions are well-stated and linked to the original research question
Additional comments: English editing of the whole manuscript is required
figure 1 the resolution needs to be improved


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

Input:
Title: IDENTIFYING BIOMARKERS FOR EVALUATING WOUND EXTENT AND AGE IN THE CONTUSED MUSCLE OF RATS USING MICROARRAY ANALYSIS: A PILOT STUDY
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comments
Experimental design: very nice experimental design
Validity of the findings: no comments
Additional comments: The authors have taken the reviewer's comments into consideration and made all required changes to their manuscript.


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

Input:
Title: UNIQUE SPICULES MAY CONFOUND SPECIES DIFFERENTIATION: TAXONOMY AND BIOGEOGRAPHY OF MELONANCHORA CARTER, 1874 AND TWO NEW RELATED GENERA (MYXILLIDAE: POECILOSCLERIDA) FROM THE OKHOTSK SEA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The MS is a great piece of work, well written and clearly argued, but could benefit from improving the English expression, numerous misspellings and incorrect word usage. I suggest that the authors engage a professional English language expert to check the MS before re-submission.

The MS is referenced well and sufficient background and context is supplied

The raw data appears to be in Table 1 and I have comments on the difficult of the format below
The Figures are attractive
Experimental design: The manuscript reviews the status of species assigned to poecilosclerid genus Melonanchora Carter, finding that the three species previously thought to be Okhotsk Sea endemics belong to different genera, one of them new, and new Mediterranean species are described on the basis of differences in the megascleres as well as the microscleres.

I cannot fault the taxonomic process and many of the problems  are minor and simply style issues that relate to the way the primary author writes. They are listed in detail in the Additional comments box below

The research questions are important for conservation and the results fill an identified gap in a sponge biodiversity knowledge
Validity of the findings: The majority of findings appear to be valid, however I struggled with assessing the veracity of the taxonomic decisions in the “Remarks” sections of each new species description (e.g., that the species was new, and differs from this and that species, etc) because most of the decisions require the reader to struggle through Table 1 to find the individual spicule dimensions for the compared species (note that the “this study” specimen details are not included which makes it even harder), and the various figures, when comparing the current species with others. It is standard practise that all such comparisons are presented clearly within the “Remarks” sections, stating and comparing in one sentence the key dimensions for the compared species, all in one place, saving a huge amount of time for the reader. It is not adequate to just say, “ this and that differed in shape and dimensions”. The inclusion of all this data, in a well-argued paragraph, makes it easier for the reader to follow the co-authors decision to assign a new species; at the moment the reader has to assess the integrity of such new species by gathering all the data together to make the own, personal decision.
Additional comments: Line 146 – 155 I would advise adding the actual museum collection accession prefix for specimens listed in Section 2.1 Museum material and sample treatment because they often differ from the abbreviations you currently have. For example: Museum für Naturkunde, previously known as Zoologisches Museum Berlin, Germany (ZMB) yet the specimens are listed as ZMB Por 3042 (Line 267). Here is a suggestion as to a clear style of writing might look like (from Reiswig & Kelly, 2018): Registration of type and general material. Primary and secondary type materials of new species, and additional material, are deposited in the NIWA Invertebrate Collection (NIC) at the National Institute of Water and Atmospheric Research (NIWA; formerly New Zealand Oceanographic Institute, NZOI), Greta Point, Wellington, using the prefix NIWA―, and the Museum of New Zealand Te Papa Tongarewa (formerly National Museum of New Zealand, NMNZ), using the prefix NMNZ PO.―.

Line 242 – You have established the new subgenus, Melonanchora (Toretendalia) subgen. nov., which necessitates the type species being set up in its own, new, subgenus Melonanchora (Melonanchora) Carter, 1874 subgen. nov. Please add “subgen. nov.” after the subgenus on line 242 so that it reads: Subgenus Melonanchora Carter, 1874 subgen. nov.

Line 242 – You say in the Remarks section to “see remarks for M(T) subgen. nov. It is preferable that the remarks that relate to Melonanchora (Melonanchora) Carter, 1874 subgen. nov. are given here, rather than making the reader try to find these former comments. Please bring them into the remarks section here.

Lines 268 & 270 (and throughout) – It is usual to write the latitudes and longitudes in the decimal format currently. Unless you can provide a good reason for not doing this (e.g. the record is a historical record that you have not collected), then it would be good to see these done throughout.

Line 265 – It is usual to italicise the name of collecting vessels. Please write the name of the vessel (and all others) as HMS Porcupine, without the quotes. Please check throughout MS.

Line 305 – ‘..any clearly discernible patter.’ Pattern

Line 338 – M. elliptica is a common…..Never abbreviate a genus name that starts a sentence

Line 354 – ‘….collected during the ‘Porcupine’ expedition in…’ Please check the details and change this to ‘…collected during the HMS Porcupine Expedition (1869) in the Northwest Atlantic (Carter….’. Please also check this annotation throughout the MS.

Line 595 –599 ‘…Additionally, it has been suggested that…’ Is this really the best place for this statement? Wouldn’t it be better up with M. cf emphysema, drawing in the environmental argument into that species? The statement here is distracting even though I can see why you are adding it in (to strengthen your argument that tumultosa is not elliptica even though they co-occur), but it is not relevant to tumultosa at this stage?

Line 606 – If M(M) intermedia is closest to M(M) emphysema – shouldn’t you place this species description just after the latter for a better comparison?

Line 659 – I note that most of the species “Remarks” sections for the species descriptions require the reader to struggle through Table 1 to find the comparative spicule dimensions for species (note that the “this study” specimen details are not included which makes it even harder), and the various figures, when comparing the current species with others.

It is standard practise that all such comparisons are presented clearly within the “Remarks” sections, outlining, and stating the key dimensions for the compared species, all in one place, saving a huge amount of time for the reader.

A good example is Line 724-725: “Differences in shape and size between microscleres of both species support that M. insulsa is a different species from M. elliptica.”

It would be much better to read about the dimension differences right here so that I don’t have to go to Table 1 and find the dimensions. This also makes it easier for the reader to assess the integrity of such new species -the reader is left to get all the data together for themselves to make the decision. Please consider expanding these sections.

Lines 831-847 Integrity of Melonanchora (Toretendalia) globogilva Lehnert, Stone & Heimler, 2006a, from the Aleutian Islands. I can see you have struggled a little with the decision to erect a new subgenus or a new genus for this unusual species. Although this new species shares several morphological characters with M(M), it is the only Pacific representative of the genus (thus extremely rare) and it has full acanthostyles (that don’t appear to be simply modified styles) and VERY unusual box-like spicules that, I think, are no more close to spherancoras than placochelae of Placospongia and anisoplacochelae of Asbestopluma anisoplacochela! However, that is for you to judge. With a slightly more indepth comparison with these other genera, it might be possible to propose a new genus, Toretendalia gen. nov., as there is (in my opinion) enough to work on. This would require a little more information on the skeletal differentiation between the genera. Something to consider anyway. I will leave this decision to you.

Line 1084 – “Skeleton: Typical of the genus”. This looks like a short-cut! – please explain the skeleton architecture as you have for everything else and this is the type taxon.

Line 1105 – These look remarkably like Abyssochelae! No response required but might be worth a comment

Table 1 – While this is indeed an impressive table, it would be very helpful to have the specimen accession number in column 1 as there is no clear reference back to your study – and very frustrating if you are trying to track a specific specimen measurement.


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: UNIQUE SPICULES MAY CONFOUND SPECIES DIFFERENTIATION: TAXONOMY AND BIOGEOGRAPHY OF MELONANCHORA CARTER, 1874 AND TWO NEW RELATED GENERA (MYXILLIDAE: POECILOSCLERIDA) FROM THE OKHOTSK SEA
Review round: 1
Reviewer: 2

Output:
Basic reporting: Language requires some more work in terms of both spelling and grammar, marked up directly on the MS PDF, but would benefit from a final check by a native English speaker once referees comments/ corrections are attended to, and before the MS is resubmitted for publication.
The relevant literature is thoroughly reviewed and exhaustedly documented, most of which is required to support the authors’ decisions. Ideally the literature citations should include DOIs (or BHL) digital links as required my many journals nowadays, where available, but I am not sure if this is a requirement of PeerJ.
The illustrations are of reasonable quality and all are necessary to support the taxonomic descriptions and decisions made by the authors.
The Table is rather long and might be difficult to publish, and might be more easily reported as a series of smaller tables?
Experimental design: The methodology is standard for these sorts of taxonomic papers, and adequately reported in the MS. One outstanding feature of this MS is the depth and breadth of the material examined from multiple collections, making it a top class, comprehensive taxonomic revision and highly important to this particular group of myxillids as a benchmark for future research on these sponges.
As mentioned elsewhere, despite the authors’ attempts, they were unable to get quality DNA to sequence the “standard barcoding” CO1 gene, which is a weakness but not uncommon with old collections with poor preservation history, and apparently for sponges in general.
Validity of the findings: The taxonomic conclusions are well-supported by both raw and analysed data/ specimens. The biogeographical component is somewhat speculative, based mostly on the literature, but without an unequivocal fossil record and molecular data, this probably can’t be improved – nevertheless, I recommend leaving it in the MS as it is of interest and as an hypothesis yet to be thoroughly tested in the future.
Additional comments: This is an outstanding, thoroughly researched contribution to the taxonomy of a relatively small group of geographically restricted myxillid sponges. It is based on accumulating and thoroughly redescribing a large collection from multiple museums and private collections, leading to a significant revision of known species, new species and new genera and subgenera. In my opinion the taxonomic decisions made by the authors are justifiable and well-defendable, and unfortunately despite their attempts to sequence old collections, would have been more strongly supported with molecular sequence data (a common problem in sponge taxonomy based on old material). Hopefully, at some time in the future, our technologies will have evolved to overcome this problem.


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: WEARABLE TECHNOLOGY TO INFORM THE PREDICTION AND DIAGNOSIS OF CARDIORESPIRATORY EVENTS: A SCOPING REVIEW
Review round: 1
Reviewer: 1

Output:
Basic reporting: In this article, Khungaqji et al provide a systematic review of how physiological data from wearable technology is used to assist clinical decision making. The aim of the review was to map out the current body of literature to identify knowledge gaps and thereby inform future research in the cardio-respiratory field. The English used is proficient, the references appear appropriate and the rationale for the study is presented clearly.
Experimental design: The methods used for the literature review appear appropriately described and executed. The review appears appropriately organised.
Validity of the findings: Within the introduction, the authors correctly state that the literature to date has focussed on the design, reliability and validity of these devices in controlled settings, and that the next phase is to translate this data into clinical useful decision making.
The conclusion states that although wearables are able to accurately collect physiological data, there is a need for specialist physicians to review the raw data before making a definitive diagnosis. They also comment on the lack of data from the respiratory domain, and a large bias towards AF detection in the cardiovascular domain. These are all correct, and point towards the current limitations in both sensor technology and the software algorithms designed to interpret the raw data which they provide.
Additional comments: The article is clearly written and the methodology, findings and conclusions are all appropriate. The discussion provides further details about the current gaps in the literature and also some of the limitations of the current technologies. In terms of answering the aims of the review, in providing a detailed map of the current literature, the authors have successfully identified current knowledge gaps and areas for future research including: 1) Application of wearable devices for clinical decision making; 2) Extending the use of these devices outside the diagnosis of AF within the cardiovascular domain and 3) The use of wearable devices for respiratory conditions. The latter appears to be an area with a significant knowledge gap.


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: WEARABLE TECHNOLOGY TO INFORM THE PREDICTION AND DIAGNOSIS OF CARDIORESPIRATORY EVENTS: A SCOPING REVIEW
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment.
Experimental design: 1. The authors are addressing a timely issue, in wearable tech and cardiorespiratory decision making. On the face of it, this number of articles seems quite low for my anecdotal observations of the literature, as well as clinical practice. For example, our study about smart watch and afib was recently published but not included here (10.1001/jamanetworkopen.2021.5821). I am not requesting you cite my work (it may fall out of the study period), it simply provides an immediate example of my concerns related to the search. I provide additional issues related to respiratory below. Also, health systems are suing "hospital at home" nowadays- would these types of articles provide relevant articles?

2. Study reports no respiratory studies, which seems incorrect. On quick Google search, I found doi: 10.2196/10046. Is this study applicable? Search criteria includes "respiratory" but not "pulmonary," which could be an issue. Also see DOI: 10.2147/COPD.S193037. Also, COVID-specific searches could change the number of resulting manuscripts.

3. Clinical decision making is part of the search. I think this needs to be better defined in the text. For example, decision making by the clinician? Decision making by the patient or someone lese? I wonder if this part of the query really limits the results.
Validity of the findings: 4. "To date, studies employing wearables to facilitate clinical decisions have largely focused
upon the cardiovascular domain." This does not seem like a conclusion since the denominator is limited to CV studies.
Additional comments: 5. The biggest gap is prospective, randomized studies link to health outcomes, which was not mentioned in "gaps." Also, what about issues surrounding integration with electronic health records/interoperability?


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: EFFECTS OF SHORT-TERM NITROGEN AND PHOSPHORUS ADDITION ON LEAF STOICHIOMETRY OF A DOMINANT ALPINE GRASS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Clear and unambiguous, professional English used throughout
Comments: English writing is not authentic. Too many long sentences make it difficult for readers to read this article. Some sentences are difficult to follow. For example, Line 12-14 “The effects of increasing N and P deposition on nutrient concentration and stoichiometry of soil and plant are gaining improving recognition, but it is unclear whether and how the mechanism of N cycle coupled with P of the soil-plant system response to increasing imbalance external N and P supply in alpine grassland” would be better to understand if change it to “The effects of increasing N and P deposition on nutrient concentration and stoichiometry of soil and plant are gaining improving recognition. However, whether and how the responses of N cycle coupled with P of the soil-plant system to external N and P deposition in alpine grassland is still unclear”. I suggest the author find a native English speaker or an ecological expert who is good at English articles writing to further polish the English language.

Literature references, sufficient field background/context provided
Comments: No comments

Professional article structure, figures, tables. Raw data shared
Comments: Results are too brief. The results should first show whether the addition of nitrogen or phosphorus significantly affects the relevant variables (show F and P value), and then at least explain which level treatment significantly improves or reduces the variable and the extent of change compared with the control. For example,
I have found an interesting pattern that N1, N3, and N7 significantly elevated NO3--N, but other levels did not affect it. Why? I suggest authors explain it.

Self-contained with relevant results to hypotheses
Comments: No comments
Experimental design: Original primary research within Aims and Scope of the journal.
Comment: Yes
Research question well defined, relevant & meaningful. It is stated how research fills an identified knowledge gap.
Comment: Yes
Rigorous investigation performed to a high technical & ethical standard.
Comment: Yes
Methods described with sufficient detail & information to replicate.
The description of the method section is too brief. Randomized block design or completely randomized design? What was the way of fertilization? What was the fertilization time? What were the rules for leaf selection? How many plant leaves are collected in each sample plot or how many weight leaves are collected? How is the soil preserved? What is the concentration of soil KCl extract? How long will it take? The above questions need to be described in detail or given references. In addition, authors conducted regression in the last 2 figures, but only describe correlation analysis in the method.
Validity of the findings: Impact and novelty not assessed. Meaningful replication encouraged where rationale & benefit to literature is clearly stated
Comment: no comments

All underlying data have been provided; they are robust statistically sound & controlled.
Comment: yes

Conclusions are well stated, linked to original research question & limited to supporting results
Comment: yes
Additional comments: 1.The author used “leaf nutrient concentration” and “stoichiometry” at the same time in the MS. These two words have the same meaning, I suggest change ““leaf nutrient concentration” to “stoichiometry”.
2. The numbers in many units in the text should be superscript, such as line 17, line 93-96, please check the whole MS, and revise it.
3. There should be a space between the number and the unit, such as line 97-98. please check the whole MS, and revise it.
4. Fig. 1 The data of ammonium nitrogen and nitrate nitrogen completely overlap and are difficult to distinguish. In addition, you say “Different small letter indicates significant difference between treatments” in the title, but where are the letters?
5. Error bars in the figures are SD or SE, clarify.
6. R2 value should be displayed in Fig 3A
7. change “correlation” to “regression” in Fig. 4 and Fig. 5


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: EFFECTS OF SHORT-TERM NITROGEN AND PHOSPHORUS ADDITION ON LEAF STOICHIOMETRY OF A DOMINANT ALPINE GRASS
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Common comment
The authors reported the effects of short-term nutrient addition on leaf nutrient concentration and stoichiometry of a dominant alpine grass. I think the research is interesting and valuable. The manuscript is well organized and has provided sound conclusion. I cannot find many errors in the manuscript. The language is ok, but it would be easier to read if the authors double-check the grammar and improve the expression. However, there are still some small errors need to be addressed. Thus, in the present form of the manuscript, I suggest a minor revision should be made before the publication in the journal PeerJ.

Specific comment

Abstract
1.	I suggest the authors add crucial and detailed stoichiometry data in the abstract.
2.	“Nutrient addition” is far too ambiguous and I suggest the author change the expression with detailed treatments.

Introduction
1.	Please provide your scientific hypothesis in the introduction section, which is essential to fully report your work.
Materials and methods
1.	Please provide detailed collection procedure of the plant and soil samples. What kind of leaf was collected? Young or old leaf?
2.	Please specify what tests were done for the general linear regression models and ANOVA.

Results
1.	The authors should show the detailed data for all the results.
2.	I suggest the authors expand the results section. The current results were far too simple and showed very limited results.
3.	No results for basic properties of plant and soil samples? I understand the authors may focus on C:N:P stochiometry, however, basic properties are useful and even necessary.

Language
1.	The language of the manuscript is not too bad, but may be better if the authors ask an English-speaker to polish the language.
2.	Please check the grammar throughout the manuscript.

Tables and figures
1.	Please improve the quality of all figures, which are difficult to read.
2.	Use typical expression of numbers instead of “-.523”.


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: EFFECTS OF SHORT-TERM NITROGEN AND PHOSPHORUS ADDITION ON LEAF STOICHIOMETRY OF A DOMINANT ALPINE GRASS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The author respond all my concerns in detail and made carefully revisions according to my comments. The manuscript has been greatly improved. I don't find any other problems with this paper, so I suggest to accept this paper
Experimental design: No comments
Validity of the findings: No comments
Additional comments: No comments


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

Input:
Title: EFFECTS OF SHORT-TERM NITROGEN AND PHOSPHORUS ADDITION ON LEAF STOICHIOMETRY OF A DOMINANT ALPINE GRASS
Review round: 2
Reviewer: 2

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


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

Input:
Title: IDENTIFICATION OF HMMR AS A PROGNOSTIC BIOMARKER FOR PATIENTS WITH LUNG ADENOCARCINOMA VIA INTEGRATED BIOINFORMATICS ANALYSIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: In the manuscript titled "Identification of HMMR as a prognostic biomarker..." Li et. al have shown methodically and logically that HMMR might serve as a potential independent prognostic factor for LUAD patients. The paper is well written with proper literature references and background/context. The writing is easy to follow and their conclusions are logical and accurately based on their analyses and observations. I have only some minor suggestions which I think will enhance the quality of the manuscript.
Experimental design: Their questions were well defined and experiments were designed accordingly. Methods have been decribed in sufficient details in my opinion.
Validity of the findings: For all experiments and analyses the conclusions are logical and well stated at the end of the experiment/analysis. All data have been provided and they appear robust and statistically sound.
Additional comments: I have the following minor comments for the authors:
1. For figure 4B, could you please explain how you identified 19 DEGs from 24 as candidate hub genes (line 161-163). Its not clearly stated there.
2. In figure 5A, please mention the names of the 4 proteins in TCGA and GSE31210 that do not overlap with each other. It will be interesting to show (encouraged) the corresponding data (similar to 5B-G) for one or more of these 4 proteins as controls.
3. Please state clearly the difference between figure 5D and E in the text and the legend.
4. Line 171 there seems to be a mislabeling. Fig 5E and F should be H and I.
5. In figure 6F, why DFS has been provided instead of PFS like in the other datasets. If DFS is shown for one, it should be shown for ther three datasets too. Please mae the figure panels consistent with each other so that its easier for readers to follow the figures.
6. The whole section of "HMMR co-expressed with FOXM1" starting from line 191 seems out of context and sudden as no mention of FOXM1 has been made prior to this in the results section. So a few lines should be added in the beginning of the section stating why FOXM1 was selected for testing its correlation with HMMR.
7. Is there any inhibitor for HMMR currently undergoing preclinical/clinical testing anywhere in the world? Would be nice to comment a few lines on this in the discussion section.


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: IDENTIFICATION OF HMMR AS A PROGNOSTIC BIOMARKER FOR PATIENTS WITH LUNG ADENOCARCINOMA VIA INTEGRATED BIOINFORMATICS ANALYSIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Zhaodong Li et al has done an integrated bioinformatics analysis to identify HMMR as a prognostic biomarker for patients with lung adenocarcinoma. Considering the severity of LUAD, this is a very interesting study to identify biomarkers using unbiased LUAD datasets.

Comments to improve:
1)Though the manuscript is written with commendable language, references to previous study in liver/hepatocellular carcinoma with HMMR using similar bioinformatics analysis, like the one published by Donglan Lu in Oncol Lett. 2020 Sep; 20(3): 2645–2654 is not included in introduction or discussion.

2)1)	The authors at line 60-63 claim that “many studies have identified hundreds of differentially expressed genes (DEGs) and indicated corresponding biological pathways associated with lung cancer, the results were not consistent because of various reasons”. Reports must be cited to for the above argument. Also, a brief information about the available biomarkers for LUAD and its associated limitations in LUAD would strengthen the case for this study in line 60-63.
Experimental design: The authors have used several reliable and established tools for their analysis. However, there are lot of technical issues with many of the analysis, which must be addressed to strengthen the observations.

Comments to improve
1) Areas like methodology, figure legends etc. are very poorly described, which must be elaborated for easy understanding of the readers. For instance, meta-analysis done in Figure 6K has very minimal information in methodology which makes the readers of different field very difficult to understand. All the experimental design has to be well described in material and methods section.
Validity of the findings: Though similar study is done and HMMR was identified as a good canditate gene in hepatocellular carcinoma using same bioinformatics approach, it is still a meaningful replication and links HMMR with LUAD. However there are many major concerns which should be addressed.

Major Comments to improve:

2)	List of genes (115 DEGs) should be included in supplementary as it forms an important piece of data for all the analysis.
3)	In Figure 3B and 3C, the criteria used for biological process analysis and pathway analysis must be described in materials section. Also, Figure 3B and C describes the percentage of enrichment. Are these percentages significant?  It is more reliable to plot the chart with respect to significant P-values.
4)	Additionally, GO analysis (Molecular function and cellular component) will strengthen the authors analysis Figure 3B and C. Also, it’s surprising to see the cancer associated pathways being not enriched in LUNG cancer datasets analyzed in Figure 3C.  A more comprehensive and stringent analysis is needed for Figure 3B and 3C.
5)	The authors have mentioned about 24 genes in line 154-155. A more detailed interpretation about this key module is required. It is important to elaborate on whether these genes belong to upregulated and/or downregulated or combination of both in results section.
6)	The authors selected HMMR based on its shared presence among top three genes strongly correlated with tumor stage. The other hub genes were just omitted, although a strong correlation with tumor stage with very significant p-values were shown in Table 1.   Though HMMR looks very interesting gene in LUAD (Figure 5A_C), unfortunately HMMR was selected just by comparing GSE31210 and TCGA. The authors should also include other datasets used in this study (GSE18842, GSE19188, GSE75037 and GSE101929) before concluding HMMR as a strong candidate gene in LUAD.
7)	HMMR over expression is very evident in Figure 5B-F between normal and tumor tissue samples. However, when tumor stages were compared with respect to HMMR expression levels, a great correlation was not obtained based on R values, though p-values are significant. The authors may need to discuss this part more elaborately in results section in line 170-171.
8)	Figure 5 H and I have no mention in the text. Also, KIF11 qRT-PCR was included, which has not been discussed elsewhere in the manuscript.
9)	As HMMR was selected by comparing GSE31210 and TCGA, survival analysis for GSE31210 dataset, if available, is mandated to strengthen the current observations in Figure 5.
10)	The authors have calculated P-values at 0.50 survival probability. The authors need to clarify and/or reanalyze why P-values were not calculated for overall survival probability in Figure 6A-F, unlike in Figure 6 G-H and Figure 7B.
11)	HMMR and FOXM1 were positively correlated in LUAD. Briefly reporting the known function of FOXM1 in LUAD in line 198-199 would enhance the significance of FOXM1 correlation with HMMR in the current study. Also, FOXM1 was lightly used in the study, an elaborate description of FOXM1 in LUAD is required in results section in line191 -199.
12)	Line 201-203 is misleading. Is the analysis done using upregulated hub genes as mentioned in line 113-114? If so, does part of this result overlap with Figure 3C? The authors need to clarify this portion.
Minor Comments to improve
1)	Misrepresentation in Figure 1 where HMMR was not identified from Gene enrichment analysis instead it was identified from shared hub gene of GSE31210 and TCGA. Arrow should be drawn from Identification of candidate hub gene to core gene identification.
2)	X-axis of Figure 6 mentions time(years) whereas X-axis of Figure 7 mentions time(year). Following a uniform labeling is required.
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: IDENTIFICATION OF HMMR AS A PROGNOSTIC BIOMARKER FOR PATIENTS WITH LUNG ADENOCARCINOMA VIA INTEGRATED BIOINFORMATICS ANALYSIS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript is presented in clear language with proper context and background. The figures are relevant, with a few minor mistakes in figure labeling that has been pointed out below. The authors address a relevant question that can potentially take the field forward with the identification of a gene that can be used as a prognostic marker for lung adenocarcinoma.
Experimental design: In the work provided, the authors analyzed multiple gene expression databases and associated bioinformatic studies to determine a potential core gene that can be used as a prognostic marker for lung adenocarcinoma (LUAD). The work is rigorous, and reasonably well-designed analyses have been chosen to address the question in concern.
Validity of the findings: The data provided are robust and statistically sound. Conclusions are well stated and within the reach of speculations. However, on fewer occasions, the reasoning of certain selections are unclear and noted below.
Additional comments: I have a few comments to the author that needs addressing for strengthening the submission.

Figure 2 - Please add the GSE profile identifier in figure 2 a-d.

In Figure 3a – Ube2c, CEP55, CDCA3 showed a higher degree of connectivity compared to HMMR. Any comment on why any of those genes were not pursued further as a potential biomarker?

In Figure 3c, biological pathways correlation of corresponding DEGs to PL1 signaling in the cell cycle has been completely ignored in favor of the FOXM1 network, though the PLK signaling dependent pathways are overabundantly present in the data. Please explain the choice in the result section.
Similarly, for the biological processes, more importance has been given to DEG’s association with the cell cycle. The potential connection to signal transduction and cell-cell communication (though found to be associated with the DEGs), thereby influencing various cancer pathways, has been overlooked. Please explain the particular selection process in the result section.

Figure 5I – The data shows the graph for the relative expression of KIF11. If this is the quantification of the western blot provided, mislabeling?

Line 171 – mislabeling Figure 5 ‘H and I’ as ‘E and F’?

Figure 6K – For the random-effects model, GSE 31210, 42127, and 684465 were used, although two other GSE databases were available for testing but were not used. Strongly recommend adding more data set here to increase confidence. GSE68465 showed a Hazard ratio of 1.0 as well. Also, please add the GSE database 42127 in the material and methods section; missing from the list of databases provided there.

In Figure 7B, the expression of HMMR above the age of 65 significantly impacted the survival rate, as shown in KM graph. Any comment or discussion on why that could be the result?

In the discussion section, the authors claimed to have provided robust evidence for the therapeutic role of HMMR in LUAD. All the data provided suggest a prognostic role of HMMR in LUAD. Please edit the sentence accordingly.


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

Input:
Title: IDENTIFICATION OF HMMR AS A PROGNOSTIC BIOMARKER FOR PATIENTS WITH LUNG ADENOCARCINOMA VIA INTEGRATED BIOINFORMATICS ANALYSIS
Review round: 2
Reviewer: 1

Output:
Basic reporting: No Comment
Experimental design: No Comment
Validity of the findings: No Comment
Additional comments: The authors have addressed all my concerns, and the paper is now suitable for 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: IDENTIFICATION OF HMMR AS A PROGNOSTIC BIOMARKER FOR PATIENTS WITH LUNG ADENOCARCINOMA VIA INTEGRATED BIOINFORMATICS ANALYSIS
Review round: 2
Reviewer: 2

Output:
Basic reporting: Zhaodong Li et al has done an integrated bioinformatics analysis to identify HMMR as a prognostic biomarker for patients with lung adenocarcinoma. This study is well written with extensive literature references/relevant background with professional English.
Experimental design: Experimental design has been clearly documented with sufficient detail and information to replicate.
Validity of the findings: The authors have extensively modified the manuscript and most of the previous concerns have been addressed very clearly. The data is statistically sound and robust and conclusions are well supported by the data provided. I strongly believe that this manuscript can be found suitable for publication in PeerJ.
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: IDENTIFICATION OF HMMR AS A PROGNOSTIC BIOMARKER FOR PATIENTS WITH LUNG ADENOCARCINOMA VIA INTEGRATED BIOINFORMATICS ANALYSIS
Review round: 2
Reviewer: 3

Output:
Basic reporting: No Comments
Experimental design: No comments
Validity of the findings: No Comments
Additional comments: A minor comment, just editing changes.
Line 191 - Probably 'non-significant' will be a better fit.

The added changes have strengthened the manuscript.


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

Input:
Title: 3D RECONSTRUCTION IDENTIFIES LOCI LINKED TO VARIATION IN ANGLE OF INDIVIDUAL SORGHUM LEAVES
Review round: 1
Reviewer: 1

Output:
Basic reporting: This research proposed an automated measurement of individual leaves and mapping variants associated with leaf angle. The reconstruction of 3D geometry of individual sorghum plants using a voxel carving method was effective, the computation of leaf angles based on curve skeleton of the 3D geometry was reasonable. Experiment design and results are reasonable and statistically sound. Some details need to be improved as follows:
Experimental design: 1.	Line 92, please explain the reason and theory support to choose five different side view angles: 0, 72, 144, 216, and 288 as side views.
2.	Line 96, since the imaged at three time points, does the illumination change with different time points? Does the illumination condition will affect the reconstruction of 3D voxels?
3.	Line 101, how many images were used for each plant to reconstruct 3D volumetric grid? Please add this detail into the manuscript.
4.	BTW, there might be a typo, “volumentric” should be change to “volumetric”.
5.	Line 111, is there any disconnection part in the voxel reconstruction model?
6.	Line 122, the definition of leaf angle was based on the principal direction of stem and leaf direction, since the principal direction of stem will change with different plants, it is a relative local angle. It would be better to convert them to an angle between leaf direction and Z axis in the same 3D coordinated system. So, the comparison of leaf angles among different plants will be reasonable and easy.
7.	Line 160, Figure 1, “B) Measurements The plant skeleton represented with measured angles for each leaf. The solid red line indicates the stem principal direction. Solid black lines represent the leaf principal directions.” Please change the description of B). The solid red line and Solid black lines should be a description in C) instead of B).
8.	Line 169, how to measure the median leaf angles and the related principal direction of stem in a manuall manner? What instrument was used? Is it possible to add one Figure to illustrate it?
9.	Line 176, what is the main reason causing the 119 reconstructions failed?
10.	There is no detail explaining the “calibrated” 2D images mentioned in the abstract. Suggest adding this into Methods part.
Validity of the findings: Experiment design and results are reasonable and statistically sound.
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: 3D RECONSTRUCTION IDENTIFIES LOCI LINKED TO VARIATION IN ANGLE OF INDIVIDUAL SORGHUM LEAVES
Review round: 1
Reviewer: 2

Output:
Basic reporting: Summary
-------------
In the manuscript “3D reconstruction identifies loci linked to variation in angle of individual sorghum leaves,” Tross and colleagues utilize a method for 3D reconstruction from multiple 2D images with a sorghum dataset from an automated greenhouse facility. The 3D reconstructions of the sorghum plants are converted to a node-edge graph structure, which are used to separate the sorghum plants into stem and leaf segments. In 3D space, the segmented plant structures were used to measure the angle between leaves and the stem to assess leaf erectness, which is a difficult trait to measure by hand. Automated 3D measurements of leaf angle had high correlation with manual measurements, even when considering measurements collected on different sets of plants in different environments. These measurements outperformed automated measurements from 2D images alone. Automated 3D leaf angle measurements were shown to be generally highly heritable and in GWAS analyses were used to identify an association peak containing the previously identified dwarf3 locus in addition to five other loci.

Strengths
-------------
- The manuscript is well-written, clear, and concise.
- The computational approach is interesting and addresses an important problem in plant phenotyping and crop development.
- The methods are complete and data and code are available for replication and reuse.

Weaknesses
-----------------
None of note.

Checks
---------
Clear and unambiguous, professional English used throughout: Yes (minor grammatical suggestions below).

Literature references, sufficient field background/context provided: Yes, the introduction was excellent and relevant literature was cited.

Professional article structure, figures, tables. Raw data shared: Yes

Self-contained with relevant results to hypotheses: Yes
Experimental design: Checks
---------
Original primary research within Aims and Scope of the journal: Yes

Research question well defined, relevant & meaningful. It is stated how research fills an identified knowledge gap: Yes

Rigorous investigation performed to a high technical & ethical standard: Yes

Methods described with sufficient detail & information to replicate: Yes, data and analysis code are shared for reuse and reproducibility. The methods in the paper are well-described and include the versions used.
Validity of the findings: Checks
---------
All underlying data have been provided; they are robust, statistically sound, & controlled: Yes, data are provided and statistical approaches are sound and documented.

Conclusions are well stated, linked to original research question & limited to supporting results: Yes, conclusions are well supported by the data.
Additional comments: Minor Suggestions
----------------------
- It is ideal to attach a license to your GitHub repository (https://github.com/mtross2/Sorghum-3D-Reconstruction) to define the conditions for use, modification, redistribution, and attribution (as applicable).
- Figure 1B (legend): Description of the colors of the lines do not match the figure.
- The quality of Supplemental Figures S2, S4, and S5 look like they were degraded by conversion to PDF. Likely just need to make sure the uploaded file type or resolution works well with the PeerJ system, the figure quality is good otherwise.

Minor grammatical suggestions
------------------------------------
- Line 59: “In sorghum, ...”
- Line 174: “An image dataset…” or “Image data…”
- Lines 175-176: Could you succinctly add why 119 timepoints failed reconstruction?
- Lines 208: “Only the first seven leaves of each plant were…”
- Line 225: “...that has been previously associated…”
- Line 227: “...the effects of additional loci on angle...”
- Line 228: “...GWAS algorithm that can...”
- Line 251: italicize dwarf3
- Line 252: “...third identified leaf at position...”
- Line 260: “Leaf angle has been shown to play a role in determining...”
- Line 293: “...true variant associations…”
- Line 309: “There are conceptually…”


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: SMALL HERBIVORES AND ABIOTIC HETEROGENEITY PROMOTE TRAIT VARIATION OF A SALTMARSH PLANT IN LOCAL COMMUNITIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript authored by Chen et al. entitled “Small herbivores and abiotic heterogeneity promote trait variation of a saltmarsh plant in local communities” uses a 22 years experimental approach to test if the presence of hares and geese have impact on the intraspecific trait variation (ITV) of Elytrigia atherica in two successional stages. They analyze height, aboveground biomass, SLA, leaf dry material content and the presence of flowers to study the ITV. Also they study genetic diversity of the mainly-clonal plant species.

The effect of this herbivorous species had a direct effect on several traits, having more marked effects at early successional stages (where the herbivory is also higher), some of the abiotic variations and genotypes also affects these traits, but are not affected by the herbivorous so no indirect effect was detected in this study.

The language used by the authors is clear, unambiguous and professional. The approximation to the questions provided in this article follow a logical order with relevant references. They introduce first the intraspecific trait variation, then explain that herbivorous can affect this variation and then they focus on the small herbivorous effects on this ITV to finally focus on hares and geese to propose the hypothesis that these small herbivorous can increase the ITV of E. atherica. I found Figure 2 very illustrative and inspiring of the results obtained, although a little repetitive. For every trait, a different diagram is represented although the effect of the herbivorous on the indirect effects is always the same. I would prefer to have only two diagrams, one per successional stage (as long as the authors can find a solution to allow the correct interpretation of the results, avoiding unnecessary overlaps between effects). Also the resolution of the figure is quite low, maybe as a result of uploading constraints.
The raw data only include the variation of traits, but not the values of this traits.
Experimental design: The experimental design is clear and well builded, not including more constraints than necessaries. Although the design has been used previously in other articles (see Chen et al. 2019) not overlap of the results were shown. The research question is also clear, and the experimental design is properly designed to answer it. The methods are properly explained and it is easy to replicate them.
Validity of the findings: The results here provided open the gate to study the effect of small herbivorus mammals (or other type of herbivorous) in the ITV of plants, with the evolutive consequences this could have. The results are also robust since 22 year dataset were used to this article. The conclusions are linked to the original question.
Additional comments: General notes and specific comments

There is a problem with the references and the bibliography section, with several studies lacking from the text or the bibliography. The proportion of new references (less than 5 years) almost reach the 50% of all the references used for this article.

L45: He and Silliman, 2016 is not cited in the bibliography

L47: Louault et al., 2005 instead of “Louault, Pillar, Aufrère, Garnier, & Soussana, 2005”

L50: I do not understand the concept of “non-borrowing invertebrates”. Also hares and geese are not invertebrates. Finally, I do not find accurate the use of “small” referring to animals between 1 and 10 kg weight. In the published articles I have consulted (Olff and Ritchie, 1998; Olofsson et al., 2004; Firn et al., 2017, 2019; Jessen et al., 2020) small herbivorous is used to define less than 1 kg weight herbivorous (e.g. voles) and others like rabbits are defined as intermediate-sized herbivorous, but in Chen et al. 2019 hares and geese are referred as small vertebrate herbivorous. I find confusing the “small herbivorous” concept and I think that adding “vertebrate”, as it was included in the abstract, it would be enough to make it clear and avoid readers to think, e.g., on invertebrate herbivorous species.

L65: Rico & Wagner, 2016 is not cited in the bibliography

L77: “Olff et al., 1997” instead of “Olff, Leeuw, Bakker, Platerink and van Wijnen, 1997”

L83: “Kuijper et al., 2004” and “Fokkema et al., 2016” are not cited in the bibliography

L93: “Boorman et al., 1998” instead of “Boorman, & Garbutt, & Barratt, 1998” and also is not cited in the bibliography

L95: “Olff et al., 1997” instead of “Olff, Leeuw, Bakker, Platerink and van Wijnen, 1997”

L102: “Chen et al., 2019” instead of “Chen et al. 2019”

L117: “Van De Koppel et al. 1996” is not cited in the bibliography, and also “Van De Koppel et al., 1996” instead of “Van De Koppel et al. 1996”

L118: “Van Der Wal et al. 1998” and “Van Der Wal et al. 2000a” are not cited in the bibliography

L118: “Schrama et al., 2015” instead “Schrama et al. 2015”

L122: “Chen et al., 2019” instead of “Chen et al. 2019”

L173: “Doyle & Doyle, 1987” is not cited in the bibliography

L174: “Bockelmann et al. (2003)” instead “Bockelmann et. al (2003)”

L176: “Sun et al., 1998” instead “Sun, Salomon, & Bothmer, 1998”

L177: “Bockelmann et al. (2003)” instead “Bockelmann et. al (2003)”

L189: “Lindsay et al., 2018” instead of “Lindsay, Clark, & Clark, 2018” and also is not cited in the bibliography

L193: “Lindsay et al., 2018” instead of “Lindsay, Clark, & Clark, 2018” and also is not cited in the bibliography

L197: “Olff et al., 1997” instead “Olff et al. 1997”

L277-278: “Schrama et al., 2012” instead of “Schrama, Berg, & Olff, 2012” and also is not cited in the bibliography.

L287: “Didiano et al. (2014)” is not cited in the bibliography

L301: “Smith et al., 2005” instead of “Smith et al. 2005” and also is not cited in the bibliography

L301-L302: “Menu et al., 2002” instead of “Menu et al. 2002” and also is not cited in the bibliography

L368: “Firn, J., J. M. McGree, E. Harvey, H. Flores-Moreno, M. Schütz, Y. M. Buckley, E. T. Borer, et al. 2020. Author Correction: Leaf nutrients, not specific leaf area, are consistent indicators of elevated nutrient inputs (Nature Ecology & Evolution, (2019), 3, 3, (400-406), 10.1038/s41559-018-0790-1). Nature Ecology and Evolution 4: 886–891.” is not cited in the text


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: SMALL HERBIVORES AND ABIOTIC HETEROGENEITY PROMOTE TRAIT VARIATION OF A SALTMARSH PLANT IN LOCAL COMMUNITIES
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript has all the basic standards for publishing a quality article. English seems to be at a high level, but I'm not a native speaker, so I leave this to the editor.
The formatting of the references seems to be fine, but the citations in the manuscript are not standardized. The order of citations is not unified, eg Line 36-37 seems to be by year, but elsewhere it is alphabetical. Furthermore, there is no uniform use of the symbol “&” versus “and” in the citation.
The structure of the manuscript is fine, however, the fact that the manuscript is based on some previous studies is a bit confusing, and the reader is not sure when reading the methodology if he is no longer reading the results.
The structure of the subchapters in the Methodology is not clear - Some chapters are in italics and something is bold. In addition, some texts of subchapters are just after the title, and elsewhere otherwise. Arrange according to the rules of the journal.
The conclusion is in italics, shouldn't it be bold like other chapters?
A few minor errors:
Line 145 - the gap between 1 and m
Line 197 - Olff et al. 1997 - complete the comma
Line 278 - Herz et al., - delete comma
Experimental design: The design of the experiment seems to be very well managed, and even the data processing seems to be fine.
Validity of the findings: As I have already written in the previous sections, the manuscript contains very well processed long-term data and is very well written. However, that's all, the interpretation of the results lags behind its possibilities. The authors beautifully explain the consequences of the obtained data, but the cause of this condition is no longer addressed anywhere. Why is selective grazing? Why do small herbivores choose specific genotypes of this plant? The literature (which is missing here, eg: Bailey et al. 1996 Journal of Range Management; Wallis De Vries et al. 1999 Oecologia; Evju et al. 2009 Oecologia; Matches (1992 Journal of Production Agriculture, et al.) is full of information about the reason for selection by different herbivores.
Herbivores: for generalists, we have two main selection pressures for this kind of selection, (1) mechanical defense of the plant (high density of trichomes, etc.); and or (2) chemical defense (increased amounts of tannins, etc. - young versus old leaves, etc.). Within one species of plant, a high variability of these traits is known (influence of genotype and/or the age of the plant). Although you did not get any data that would support it in any way, it would be very appropriate to mention it in the discussion and in the introduction. Plants can thus significantly affect the size of the herbivore population (eg Saska et al. 2021 Journal of Pest Science).
Additional comments: No additional comments