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

Input:
Title: THE SPINDLE ASSEMBLY CHECKPOINT AND SPECIATION
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors propose a mechanism by which new species can diverge from the existing population through chromosome rearrangements occurring during meiosis, allowing them to become reproductively isolated. They suggest that the dynamics of the SAC provide the mechanism to allow this speciation to occur.
In the introduction, authors state that the SAC is satisfied only by tension, however this is the subject of debate in the current literature. This conclusion has been mainly drawn from experiments using low dose taxol, a drug that stabilises microtubules and decreases inter-sister kinetochore tension. However, importantly, this drug can also generate single unattached kinetochores which are known to generate a SAC signal to delay the cell (Proudfoot et al, 2019 Cell Reports; Roscioli et al, 2019 BioRXiv, figure 4). Therefore it is difficult to separate tension from attachment in terms of SAC activation. Further experiments have shown that SAC proteins are not lost from kinetochores upon gain of tension using inter-sister kinetochore distance as a readout (Kuhn and Dumont, 2019, Journal of Cell Science). While this is not the focus of this manuscript, authors should be aware that SAC dynamics are not yet fully understood and should be cautious of any oversimplification as it does not represent the true biological mechanism.
Furthermore, authors have grossly oversimplified the mechanisms of SAC signalling in the introduction section ‘Normal operation of the spindle assembly checkpoint’ by stating that the wait signal is mediated by Aurora B. While Aurora B is the most upstream kinase involved in SAC signalling, there are many more events occurring after this. Authors must introduce downstream mechanisms, including the Bub and Mad proteins, and how they are recruited and removed from the kinetochore. They should also introduce the generation of Mitotic Checkpoint Complex (MCC), which constitutes the wait anaphase signal. Authors can refer to Musacchio and Salmon, 2007 (reference 9).
I also note that the authors introduce mitotic checkpoint signalling however the context of this analysis appears to be within meiosis. Authors should comment on the differences between mitosis, meiosis I (co-orientation) and meiosis II (bi-orientation) to make this clearer, and how this affects SAC monitoring. I appreciate authors are focusing on meiosis II for this manuscript, which is more similar to a mitotic division, but introduction of the meiosis I segregation event would help make it clearer to readers how chromosome rearrangement events arise. There is a review written by Hiroyuki Ohkura (Meiosis: an overview of key differences from mitosis 2015, Cold Spring Harb Perspect Biol) that may be of interest.
In the discussion section, authors state that chromosomal rearrangements during meiosis are not rare (line 461), but then use the point of Downs syndrome to provide evidence for this in humans. Are they referring to Down’s syndrome as trisomy 21 or translocation Downs syndrome? This is important as Downs syndrome is a result of aneuploidy leading to the egg containing 3 copies of chromosome 21. This is not a chromosomal rearrangement event but instead a chromosome mis-segregation event leading to aneuploidy. Translocation Downs syndrome, a definite chromosomal rearrangement, is much rarer. We know that meiotic aneuploidy (whole chromosome gain/loss) is high in human eggs, meanwhile meiotic aneuploidy is actually rare in other species. See Hassold and Hunt, 2001 Nature Reviews for a good overview on this.  Authors need to be more precise on whether they are discussing chromosomal rearrangements (changes within the chromosomes) or aneuploidy (gain or loss of a whole chromosome), as these have distinct mechanisms of generation.
It is also worth considering that aneuploidy in human eggs is known to increase with increasing maternal age (>35). Is this manuscript considering only human evolution or all species?

Other comments:
•	Line 72: Typo ‘chromosomas’
•	Lines 84-87. Please provide a reference for the statement that there is a 50:50 chance of attaching to each kinetochore, or if this is an assumption of your model it should be stated as such.
Experimental design: I cannot comment on the mathematical analysis done in this paper as it is not an area that I have experience in.
However, authors describe 3 attachments states; monotelic, syntelic and amphitelic (biorientated). There is also a 4th attachment state – merotelic, where one kinetochore is correctly attached while the other is simultaneously bound to microtubules originating from both spindle poles. This is an important state as it is often ‘invisible’ to SAC signalling and as such can result in whole chromosome mis-segregation events. This should be considered in the text and experimental design.
Validity of the findings: Line 431: Authors state that if one chromatid possesses two kinetochores, then the correct attachment of only one of these is sufficient to satisfy the checkpoint based on tension which will allow the cell to progress to anaphase. As stated in my earlier comments, we cannot assume that the SAC only responds to tension, therefore in my opinion this statement is untrue as the incorrectly attached second kinetochore would still signal to the SAC, and this is sufficient to delay anaphase onset (Rieder et al, 1994, Journal of cell biology). Authors need to discuss the relevance of this.
Additional comments: The manuscript has been prepared with good English. I am very intrigued by the authors hypothesis that chromosomal rearrangement and subsequent satisfaction of the SAC in the following meiotic division could be a driver of speciation. This is a very compelling idea and I think could be an important mechanism. However, I am not confident that the analysis presented in this manuscript provides strong evidence to prove this point, as there have been a lot of assumptions made that are not biologically sound. Authors could improve this by adding in merotelic attachment, as I have noted above. Authors also need to be careful with their conclusions bearing in mind that the SAC is not satisfied by tension alone.
More generally, the figures should be better annotated so that the reader can more easily follow the ideas. Figure legends should also provide more detail so that the figures can stand alone from the text and other figures. The tables are also quite hard to interpret (I am not sure if the formatting has changed between the review PDF to the original 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: THE SPINDLE ASSEMBLY CHECKPOINT AND SPECIATION
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: I thank the authors for considering all the points raised during the reviewing process. The manuscript is now improved by discussing more clearly the assumptions and alternative interpretations


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

Input:
Title: THE SPINDLE ASSEMBLY CHECKPOINT AND SPECIATION
Review round: 2
Reviewer: 2

Output:
Basic reporting: The manuscript is now much more coherent. Authors have added some further detail on SAC signalling as requested. They have also made clear that the setting of this study is meiosis II and disclosed the assumptions that this has caused them to make.
Experimental design: I am not experienced in mathematical modelling so cannot comment on this. However, the authors have now made the assumptions in their analysis clear, and discussed the caveats of this in greater depth.
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: HIGHER CARBON SEQUESTRATION POTENTIAL AND STABILITY FOR DEEP SOIL COMPARED TO SURFACE SOIL REGARDLESS OF NITROGEN ADDITION IN A SUBTROPICAL FOREST
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors provided adequate background information related to this study. The manuscript was well organized. Tables and figures are nicely presented. Hypotheses could be improved by providing explanation or reasons for the two hypotheses. English writing is fine in general. But there are a few errors and awkward sentences that need to be corrected.
Experimental design: The research is original and fit the aims and scope of the journal. Rational was provided in the introduction. Materials and methods were provided in details. For data analysis, I think the authors could test glucose addition, N addition and their interactions. Thus, a three-factor ANOVA should be used. It seems that the authors only tested the simple treatment effects (compared among CK, Glucose, N, and Glu+N treatments), plus depth.
Validity of the findings: The authors clearly provided the results, and results are generally sound. The conclusion was supported by the results.
Additional comments: Overall, this is a well-designed lab incubation experiment. Although the incubation was short, the trends of CO2 emissions were clear. Results were well presented and explained in the discussion. I don’t have any major concerns with this study, but I have two suggestions for the authors. One is the data analysis. The authors used a two-factor experimental design with N addition and glucose addition. But ANOVA only considered simple effects of four treatments. Glucose, N and their interaction could be test. Another one is that I feel that the results and conclusion of “subsoil has a greater potential in long-term C sequestration in forest ecosystems” could be caused by the experimental design. Different amounts of glucose were added to topsoil and subsoil. If the same amount of glucose was added, the results could be different. I think the authors need to address this issue, at least to discuss this point. I recommend minor revision.
Specific comments;
L16: change “(priming effect)” to “through priming effect”?
L75: change “widely founded” to “mostly found”
L87-89: Please add explanations to the two hypotheses.
L101: topsoil and subsoil: Usually subsoil is just below the topsoil. As 10-30 is transition soil layer, why did not include this layer as well?
L220: delete by
L223: t test
L288: I recommend a reference showed similar phenomena (Hui et al. 2019. Phosphorus rather than nitrogen enhances CO2 emissions in tropical forest soils: Evidence from a laboratory incubation study, EJSS).
L292-293: I don’t agree with this statement. What would happen if the same amount of glucose was added to the subsoil?
Table 2. Please add the CK to the table.


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: HIGHER CARBON SEQUESTRATION POTENTIAL AND STABILITY FOR DEEP SOIL COMPARED TO SURFACE SOIL REGARDLESS OF NITROGEN ADDITION IN A SUBTROPICAL FOREST
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: This manuscript is well and informative. However, there are still some problems that need to be revised before publication. The manuscript has two major weaknesses. First, the distribution of 13C-glucose into microorganism’s pool is lack of direct data supporting. If the author could strengthen the discussion by adding some microbial utilization mechanism will greatly improve the manuscript. Second, using the results of a short-term laboratory incubation to explore long-term phenomenon of fresh C partitioning and stabilization, thus, the results should be interpreted with caution.

L119-120 The incubation in dark? Oxygen condition? And how to control soil moisture during incubation?
L134  Why not use the same jars for CO2 efflux rate and 13C-CO2 determination?
L147  I think the Fig. 1 belong to the appendix.
L236  mg g-1 should be “ug g-1”
L242  “affect  the C” delete extra spaces
L289  “retained glucose-C mostly existed as live MBC…” Can you show the range of data for mostly? Is there really no free glucose left?
L294  Same substrate (glucose) lead to different microbial CUE of Top- and Sub- soil. This should be further explained. Microbial community compositions differ in the two depth soils? Or soil characteristics difference result in different CUE?
L306-308  I very agree with you. Long-term studies are needed. However, the limitation of the current study should be pointed out.
L321-322  “the 13C signature in WEOC unlikely comes from free glucose, but from the live MBC” need more supporting evidence.
L369  4.2 to 4.3
L397  priming effect to PE
L402-403  “suggesting that the subsoil played a greater role in the long-term C sequestration and stabilization” this conclusion should be caution due to the only 20 days lab incubation.
Figure 2, the Y-axis scale is not appropriate for A.
Table 1 WEOC data?
Table 2 The amount… unit
Table 3 I recommend the pie figure for these data.
Figure S1 The cumulative CO2 release for 13C-glucose also should be given.


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: HIGHER CARBON SEQUESTRATION POTENTIAL AND STABILITY FOR DEEP SOIL COMPARED TO SURFACE SOIL REGARDLESS OF NITROGEN ADDITION IN A SUBTROPICAL FOREST
Review round: 1
Reviewer: 3

Output:
Basic reporting: The MS "Higher carbon sequestration potential and stability for forest subsoil compared to topsoil regardless of nitrogen addition in a subtropical forest" describes an interesting work to elucidate the carbon sequestration potential of surface and subsoil in a tropical forest and how nitrogen addition could affect this carbon sequestration. Laboratory incubation experiments were performed for 20 days and 13C-labelled glucose was used as C substrate. MS is based on sound literature and background information, description of results seem adequate and practical, and discussion section is also relevant. The authors have critically discussed their hypotheses. I have provided my feedback directly to the pdf copy of the MS to help the authors during revision process
Experimental design: Experimental design is OK as are the statistical analysis. Experimental design is also practical in lieu with the hypotheses. As mentioned as comments/suggestions, I was only curious about authors not using 13C-labelled litter in their experiments.
Validity of the findings: The study provides important insights into the mechanistic understanding of potential C sequestration in surface and subsoil. The authors found non-significant effects of nitrogen on priming effect and C sequestration. Despite the advocacy of the authors, I think a cautious approach is required while applying the study interpretations at field scale and also on long-term basis. Therefore, the term "C retention" rather "C sequestration" may be more appropriate the context of the study. Level of speculation could be also be used with care
Additional comments: The MS is generally well-written and results and discussion sections have strong implications. However, at points during discussion, the authors have overlooked the role of CNP stoichiometry in C sequestration.


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: HIGHER CARBON SEQUESTRATION POTENTIAL AND STABILITY FOR DEEP SOIL COMPARED TO SURFACE SOIL REGARDLESS OF NITROGEN ADDITION IN A SUBTROPICAL FOREST
Review round: 2
Reviewer: 1

Output:
Basic reporting: This is a revised manuscript. The authors have made efforts and adequately addressed my questions. I don't have any further comments.
Experimental design: It would be better to have a full factor design. But the authors explained why no N alone was applied.
Validity of the findings: Results were well presented and explained.
Additional comments: I recommend Accept.


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: HIGHER CARBON SEQUESTRATION POTENTIAL AND STABILITY FOR DEEP SOIL COMPARED TO SURFACE SOIL REGARDLESS OF NITROGEN ADDITION IN A SUBTROPICAL FOREST
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: I’m satisfied with the author’s revision. This new version looks good.


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: HIGHER CARBON SEQUESTRATION POTENTIAL AND STABILITY FOR DEEP SOIL COMPARED TO SURFACE SOIL REGARDLESS OF NITROGEN ADDITION IN A SUBTROPICAL FOREST
Review round: 2
Reviewer: 3

Output:
Basic reporting: N/A
Experimental design: N/A
Validity of the findings: N/A
Additional comments: The authors have responded positively to the comments of the reviewers and manuscript has been revised appropriately. Overall structure and message of the manuscript has also become clear and 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: PHYLOGENETIC RELATIONSHIPS IN THE SOUTHERN AFRICAN GENUS DROSANTHEMUM (RUSCHIOIDEAE, AIZOACEAE)
Review round: 1
Reviewer: 1

Output:
Basic reporting: The writing of the manuscript is vague, with many grammar issues. I am listing a few examples below. Please check the entire manuscript carefully. In addition, in general the flow of the MS can be improved by using topic sentences to guide readers.

Line 27: “73 species represented by multiple accessions of Drosanthemum” is vague. Do you mean “73 species of Drosanthemum with multiple accessions per species”?

Line 28: “phylogenetically studied” is awkward.

Line 29: It is unclear what does it mean by “phylogenetic affinities not obvious in the phylogenetic tree”

Line 37–38: “molecular and morphologically diverse” is grammatically incorrect. Also “molecular diverse” is vague and should be reworded.

Line 120: “are nested in”, instead of “group inside”

Line 130: “More generally”, instead of “More general”

Line 281 to Line 324: paragraph very long. Break into multiple paragraphs and use topic sentences to guide readers.

Line 326: “Genetic diversity patterns” is vague. How about something like “Alignment matrices”?

Line 364: “relationships among the six lineages were weakly supported” instead of “without supported relationships”.

Line 453–459: very long sentence. Shorten or break into multiple sentences. In addition, reticulation vs. incomplete lineage sorting are two distinctive processes. They are not “consistent with” each other.

Fig. 3: specify that outgroups are removed in the figure legend, and add “Subg. ” to each of the names on the right to avoid confusion
Experimental design: In general, the sampling, marker used, and methods are appropriate for the research questions. My only minor comment is that the two cpDNA regions should be analyzed separately before concatenating them.
Validity of the findings: In general, the results are valid. Given the low variation in ITS, the phylogenetic analyses mainly relied on two cpDNA regions. It is unclear whether analysis of additional nuclear regions would recover the same phylogenetic relationship. This caveat should be explicitly addressed in Discussion.
Additional comments: Given the main focus of the MS on the phylogenetic relationships within Drosanthemum, the introduction is too long. It is unclear how this long list of character evolution and phylogenetic relationships in Aizoaceae are relevant to Drosanthemum. I would suggest the authors significantly shorten the introduction and focus on how evolution of a subset of characters relate to the evolutionary context of Drosanthemum, and remove the statement in Line 54 on “a synoptic overview on the current classification of the family”.


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: PHYLOGENETIC RELATIONSHIPS IN THE SOUTHERN AFRICAN GENUS DROSANTHEMUM (RUSCHIOIDEAE, AIZOACEAE)
Review round: 1
Reviewer: 2

Output:
Basic reporting: According to the authors, the raw data is available in the Dryad repository, but I could not check this as the link they provide was not working, I guess this is due to an embargo.
Experimental design: No comment
Validity of the findings: No comment
Additional comments: In this manuscript,the authors present a phylogenetic study of Drosanthemum with a wide taxonomic sampling (more than 60% of the genus) that clarifies the evolution of this genus. Previous studies had just focused on very few species (around 10% of the genus). The authors have conducted a thorough work to insure that specimens sequenced are well-identified, an important point givent that it is a challenging taxonomic group. Another strength of the study is that the authors included several individuals for species that are more morphologically variable and widespread.
The research questions of the study are well defined and are relevant to understand the evolution of the genus studied. The methods used and the data analysed are appropriate to fulfill the main aim of the study, and the discussion and conclusions derived from their results are sound.
The article is clearly written, the introduction provides sufficient background and is well referenced. The methods and results are clearly detailed. The discussion and conclusions are well stated.

Concerning to weaknesses of the study, I only detected minor text issues that I detail below:

-The authors speak of "pseudo-cryptic speciation", but following Bickford et al 2007 (https://doi.org/10.1016/j.tree.2006.11.004) I think it is more appropriate to speak of cryptic speciation, as it does not necessarily imply a sister relationship, among others (see the section "What are cryptic species?" of that article). In relation to this, I think that the reference to Sáez et al. 2003 (a study on coccolithophores) that the authors included when speaking of pseudo-cryptic speciation is not relevant here.

-l. 157 "extra-ordinary" should be "extraordinary"
-l. 183 replace "or" by "and", more appropriate
-l.399 typo: "haplotyp"
-l. 512: typo: "is largely confirmed a few ..." should be "is largely confirmed, a few..."
-l. 527: should say "are restricted" instead of "restricted"
-l.528: should say "extends" instead of "extend"
-l.530: should say "Ossicula are" instead of "Ossicula, are"
-l.565: rephrase the end of this sentence in a more clear way: "the, for Aizoaceae unusual, flower and fruit diversity present in the genus."
-l.573: "this is mirrored in in the" should say "this is mirrored in the"


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: PHYLOGENETIC RELATIONSHIPS IN THE SOUTHERN AFRICAN GENUS DROSANTHEMUM (RUSCHIOIDEAE, AIZOACEAE)
Review round: 1
Reviewer: 3

Output:
Basic reporting: See general comments.
Experimental design: See general comments.
Validity of the findings: See general comments.
Additional comments: Review of Phylogenetic relationships in the southern African genus Drosanthemum (Ruschioideae, Aizoaceae).
This manuscript presents an interesting phylogenetic study of an interesting genus of Aizoaceae. For the first time, authors generated a data set with good phylogenetic representation of the the genus (73 of 114 species included), based on highly informative cpDNA markers and not so informative ITS data. Moreover, they compiled an occurrence data set. With these, they reconstruct a phylogeny, but this is not formally analysed (i.e., not dealt with in "Results").  Overall, I find the study interesting and relevant, but I have some concerns regarding the presentation, especially of the ITS data.

The whole paper is rather long, and although it is reasonably well written, it includes a fair amount of unusual phrases, such as "branching artifacts" (l 243), "pseudo-cryptic species" (l 574), "biphyletic" (l 480) "molecularly homogeneous lineage" (l 177). Although these terms can be understood with some good will, they hamper the flow of the paper.

The introduction is quite long, but contains a fairly complete overview of the phylogenetic relations within the relevant parts of the family, so that it contributes to the paper.

The questions at the end of the introduction are eseentially valid, but phrased unnecessarily complex.
Q1, l177-179, is formulated in an unusual phrasing and unnecessarily vorbose, "whether Drosanthemum constitutes a coherent, molecularly homogeneous lineage sister to Ruschiaea, or whether it forms an agglomeration (or grade) of several mesomorphic lineages", while the question is plainly and simply "Is Drosanthemum a monophyletic lineage sister to Ruschiaea?". That's a fine question that doesn't need other wording. Similarly, for Q2, I would drop the words "covering all species diversity" from line 180. Simply ask whether the morphologically delineated subgenera are monophyletic.
Q 3 in essence is two questions: is subgenus Drosanthemum also monophyletic, and, does subgenus Drosanthemum contain cryptic species.  I don't see how the first aspect of Q3 is fundamentally different from Q2, as both questions deal with the circumscription of subgenera.  Therefore, you should rephrase to reflect the second aspect, namely, whether multiple accessions within species within the dustbin subgenus Drosanthemum are eachother's closest relatives.  Q4 is fine as formulated, though a formal analysis addressing this question is lacking.  If you want to do this, you could, for instance, analyse the pairwise distances between all accessions, and analyse this with a PCoA.

The methods are logically structured and complete, but they could be shortened.  In various places you present a fairly complete list of what you did, and then again explain the same information later (e.g., l 240-253 is largely superfluous). For instance, l 243 you defer dealing with "branching" artifacts to the next paragraph, but there you barely deal with it and in stead refer to SI and literature. Perhaps you can streamline all this.

The Dryad link did not yet work.

l 246-248. This is an interesting application of the EPA algorithm that I have not yet seen.  The algorithm was not designed for this application (though I suspect it should work). If you know of other studies to use it to find a root position, please cite them.
I don't really understand, however, why this approach is preferred over simply including the outgroup DNA data in a phylogenetic analysis. Does in any way it leverage information not available in a normal RAxML analysis? Apparently, they avoid what you call "ingroup outgroup branching artifacts", but you don't explain what they are, how they arise, you only refer to the SI of *another* paper for examples, so this remains unclear. Certainly, both EPA and a "normal" raxml run are based on computing the likelihood of alternative topologies so results must be very similar.

ITS data.  I think you try to make too much of this essentially not very informative marker. I think it suffices to state that including it with the cpDNA data did not alter the topology and analysing on its own did not reveal well-supported conflict with the cpDNA results. Including it within Figure 3 is very distracting and should be avoided. The cpDNA results and outgroup placement analyses indicate that the branch to the ingroup is too long to confidently place the outgroup. Hence, the cpDNA evolves too fast to be informative.  The ITS data, however, evolves too slow to infer relations within the outgroup, but that may suggest it is a useful marker to place the outgroup?

Median joining networks.  These results, in my opinion, add very little information to the paper. Mostly, they corroborate the cpDNA phylogenetic results.  Therefore, I would not include them in the main paper, they are distracting.

I'm a little disappointed that you could not make more of the distributional patterns, except discussing them briefly.  If you want to keep them, you should include a sentence or two in the results. The clades are geographically quite highly structured, but for readers not familiar with the Cape region, perhaps you can map them onto a map defining major climate types, to corroborate your discussion.

The discussion overall is interesting and reflects the intimate knowledge of the authors of the group of study.

Figures.
10 Figures is certainly a lot for this paper and in my opinion, it dilutes the valuable message of the paper unnecessarily.

Figure 1 is a a systematic classification, not the result of a phylogenetic analysis based on the data you collected.  Therefore, it is more appropriate to present it as a table. Alternatively, since your results underline this figure, you can include it as the "summary", but then it should be the last figure

Figure 2 is nice.

Figure 3 is a bit confusing.  It deals with the cpDNA, but it isnt clear what "information from ITS data" means. This is the "main tree figure".  Can't you simply do a parsimony network of the ITS data and demonstrate that it doesnt in major ways contradict the cpDNA tree?

Figure 4 is nice.

The network presented in Fig 5-8. is a bit unconventional and therefore confusing.  In particular, the circles are not proportional to the number of individuals (as is typical in a haplotype network) but to sequence divergence within clades. Overall, I don't really see the point in the light of the rest of the results. If you want to keep these figures, figs 5-8 should be collapsed into a single figure.
The reason that I don't think these figures are very important is that all they signify is that there are not a large number of mutations in the data.  Therefore, you quickly form networks.


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: PHYLOGENETIC RELATIONSHIPS IN THE SOUTHERN AFRICAN GENUS DROSANTHEMUM (RUSCHIOIDEAE, AIZOACEAE)
Review round: 2
Reviewer: 1

Output:
Basic reporting: No additional comments.
Experimental design: No additional comments.
Validity of the findings: No additional comments.
Additional comments: The authors did a nice job improving the manuscript. I only have a few very minor wording suggestions.

Line 84: “First-branching” is vague. How about “sister to the rest of Aizoaceae”?

Line 243: Do you mean “partitioning” instead of “portioning”?

Line 336: “among” instead of “between” the six lineages.

Line 436: Given potential concerted evolution in the ITS region, and there is no real test for the population size, it is unclear that there is  support for an “initial bottleneck”. Perhaps remove this as it is not essential to the main questions of this MS.

Table 1: without some grid lines it is not very intuitive what are included in “Mesembs” and which “core ruschioids"


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: PHYLOGENETIC RELATIONSHIPS IN THE SOUTHERN AFRICAN GENUS DROSANTHEMUM (RUSCHIOIDEAE, AIZOACEAE)
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The authors have successfully responded to the (minor) concerns of my previous review. I therefore recommend the publication of 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: PHYLOGENETIC RELATIONSHIPS IN THE SOUTHERN AFRICAN GENUS DROSANTHEMUM (RUSCHIOIDEAE, AIZOACEAE)
Review round: 2
Reviewer: 3

Output:
Basic reporting: no additional comments
Experimental design: no additional comments
Validity of the findings: no additional comments
Additional comments: The authors have provided a careful revision of the paper, where they incorporated many of the points I previously raised.  In particular, the readability of the paper is considerably improved by rephrasing the questions at the end of the introduction, and restructuring elsewhere.  The authors did not agree with me on all fronts, but the parts where our opinions diverge are largely matters of presenting results, rather than their validity.

A few minor remarks:
- I don't intuitively understand the rank of the informal names "Mesembs" and "core ruschioids" in Table 1.  It would be helpful to point this out, e.g. with footnotes.

Fig 2. In the legend, "Edge lengths are scaled on expected number of substitutions" should probably read "Edge lengths are drawn proportional to the expected number of substitutions per site".


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: CHARACTERISTICS OF THE SOIL MICROBIAL COMMUNITY IN THE FORESTLAND OF CAMELLIA OLEIFERA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The English language of the manuscript is generally clear and understandable, but there are grammatical errors (e.g. “studies has”, l. 50) and incorrectly used words that cause some confusion (e.g. “soil oxidation” l. 42). The manuscript would benefit from proof-reading by a fluent first-language speaker.

The introduction is missing any literature background on soil microbial community analysis, including previous community characterization and how this relates to the present study.

The article is logically structured and easy to follow.

Figures are of high quality, although not all are well explained and some might be unnecessary (see further comments below).

It is not stated at what cultivation time point Figure 2 was measured (with respect to Figure 1).

To my knowledge, Figures 3 and 4 are rarefaction curves, not dilution curves.

Figures 7 and 8 Not clear if this is for rhizosphere soil or bulk soil.

The manuscript forms and appropriate, self-contained “unit of publication”
Experimental design: The manuscript fits well within the aims and scope of PeerJ.

The research question (determining the soil microbial community structure under C. oleifera) was reasonably clear, but the authors could better explain why this is relevant or important. A knowledge gap was not clearly identified.

There are several points of concern about the technical rigor with which the study was conducted, and the handling of the results:

1) I found it very surprising that so few OTUs were observed, especially for N4, N5 and N6 (Fig 1 and 2, line 290). Most remarkably, Figure 12 indicates that the fungal communities of N5 and N6 consist almost entirely of one genus! It would be good to know what steps were taken to check that no unusual artefacts were introduced during extraction, library prep or sequencing. Are the authors confident that these really reflect the diversity of these soil samples? This concern arises again in line 190-191, where it is reported that the 14 dominant non-rhizosphere bacterial species (OTUs?) accounted for 76% of total abundance – implying numerous OTUs with >5% of total abundance – a surprisingly simple community for soil.
2) Statistical significance in Table 1 seems incorrect. It is not stated what the uncertainty measures are (standard deviation or standard error? – this should be indicated). But even if these are standard deviations, it is not feasible that (for example) 5.2 +/- 0.29 and 5.33 +/- 1.14 could be significantly different (pH of non-rhizosphere soil in summer and autumn).
3) Figure 7 and 8 miss the point of a Venn diagram – the areas should be proportional to the values, otherwise the graphical representation has no meaning.
4) I doubt whether the PCA analysis actually provides useful information from this data, since the principle components seem to be mainly accounting for two outlier samples (I wonder whether these are N5 and N6?).

The Methods section is insufficient to allow for replication. In particular, it provides very little information on the procedures and conditions used for amplification and sequencing, and no information at all on bioinformatics analysis (e.g., which R packages, with what steps taken).

The Methods section should also provide a bit more information on the enzyme measurement procedures, and include a reference for the cellulase activity determination.

In line 81-83, some basic information on the sampling should be provided, at least including: sampling depth; separation of rhizosphere and non-rhizosphere soil; pooling of samples (this is clear from the data, but it is not clear in the Methods section whether the 15 trees are replicates are not); sieving.

I did not identify any ethical problems with the manuscript.
Validity of the findings: Concerns regarding the data and statistics have been noted above.

I was not able to open the background data files linked in the manuscript submission.

The manuscript does not mention the depositing of sequence data in an appropriate repository (e.g. NCBI), although this would be the norm for such a study.

Lines 29-30, and line 295, state that pH, available P and urease activity were “dominant influential factors for the soil microbial community”, but the data presented in the manuscript does not allow the direction of causality to be determined (even though, for pH and available P, it is already established in the wider literature).

Line 287-288 concludes that the “fertility” of the rhizosphere soil was superior, but “fertility” was never defined and it is unclear how this conclusion can be arrived at from the presented data.

Line 289-290 call the rhizosphere microbiota “superior”, but this value judgement is not defined in the manuscript.

The Biolog plates that were used to estimate functional diversity contain a range of very different chemical substances. It is not clear how these varied chemicals were grouped into just six categories (Figure 2, lines 245-247) and if this can actually say anything meaningful about function. For example, I assume lactose and glycogen were grouped under “Saccharides”, but how is it meaningful to consider these together? An ordination method might be more appropriate for analysing this data.

Figure 10 and lines 203-210 seemingly present data on functional genes in the community, but it is not explained where this data comes from or how it should be interpreted. The functions that are listed are all standard cellular housekeeping functions, so it is not clear what helpful information this gives about the soil community’s ecological function. Unless the authors can connect this to the interpretation of other data, I would suggest to remove this.

Line 222-223 conclude that microbial biomass and enzyme activities are good indicators of soil quality, but this cannot be concluded from the presented data, which did not contain any direct measures of soil quality (e.g. plant performance).

Lines 259-260 state that the dominant microbial groups are the basis of the soil’s function, but this is not demonstrated by the data, and it is not safe to assume that the most abundant taxa necessarily are the most important for function.

Lines 275-276 seem like speculation. This requires either supporting literature or a clearer link to the data.
Additional comments: Line 34-35 suggest an application of the findings, but this is not adequately explained in the text.

Line 38 “photo-contracted” should be “Photosynthetically fixed” or something similar.

Line 49 “buffering capacity” is not a good word to use here, due to its usual meaning in terms of pH buffering.

Are the sampled ecosystems really “forests” (which implies some level of natural function) or are they really plantations?

Line 74 Please provide a soil name in accordance with the World Reference Base, so that an international audience can easily understand the soil conditions.

Line 90 needs reference for alkali-hydrolysis diffusion method

Line 92 “resistance colorimetric method” unclear why resistance – not just a standard colorimetric / absorption method?

In the Results, I would encourage the authors not to repeat results in the text that is more easily understandable in tables or figures (e.g. lines 119-123), unless there is a clear reason to highlight one or two values of particular importance.

Line 163 – “airborne” not clear what this refers to

Line 171-172 The comparison here is not clear.

Various places, e.g. line 175, “OUT” should be “OTU”

The authors should carefully consider when it is appropriate to use the word “species” (in my view, when a species has been taxonomically defined), and when to use “OTU” (when it is based solely on a phylogenetic interpretation of the present data).

Line 198 It is unclear what “abundance” refers to here.

Lines 252-253 claim that rhizosphere soil should be more resistant to environmental soil, but this seems like speculation rather than an argument based on the presented data. This might be a missed opportunity, because the seasonal sample in this study might allow an analysis of which communities were more resistant and/or resilient to seasonal environmental changes.


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: CHARACTERISTICS OF THE SOIL MICROBIAL COMMUNITY IN THE FORESTLAND OF CAMELLIA OLEIFERA
Review round: 1
Reviewer: 2

Output:
Basic reporting: There are many significant issues with this manuscript.  For example,
1)No objectives and hypotheses are given.Hence there are no research questions.
2) Methods are not stated clearly and important information lacking e.g. conditions for molecular work and hence does not allow for meaningful replication.
3) In abstract, where the term, "greater than" is stated, there must be sound statistically evidence to support this. However, non was given.
4) Headings are not clear
5) Line 65-66 states.. "it is necessary to understand such information..... why is this so? 6) What is the significance to this study? How does it contribute to the gap in the literature and what is this gap? All these are very important questions that must be stated and addressed in a scientific study as this. However, these are lacking.
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: CHARACTERISTICS OF THE SOIL MICROBIAL COMMUNITY IN THE FORESTLAND OF CAMELLIA OLEIFERA
Review round: 3
Reviewer: 1

Output:
Basic reporting: - Literature background on soil microbial community analysis

In l. 64-71 the authors have added some commentary on laboratory culture studies, but it would be useful to have some context of the relevant microbiome research.

It is stated that “high throughput sequencing can reflect soil microbial community structure comprehensively and accurately” but this is not the case, as it suffers from numerous biases, e.g. (Větrovský and Baldrian, 2013), so this should be stated less strongly.

- Soil description according to the FAO World Reference Base

The authors have not described the soil in terms of FAO-WRB nomenclature, which would be very useful for readers from other regions of the world.

- There are various errors of English grammar, and the manuscript would benefit from proof-reading by a first-language speaker.
Experimental design: - Very few OTUs observed, especially for fungi in N5 and N6

The authors acknowledge that they were also surprised by these results. They try to explain the finding in terms of ecology (though not found in other replicates). However, it important first to demonstrate that the result is correct. It would be helpful to know what was done to make sure that these results were accurate. For example: Were the samples resequenced? Were mock communities properly sequenced with these samples? If the authors cannot provide assurance that this was not caused by experimental problems in sequencing, then this possibility should be acknowledged.

- Potential distortion of PCA by outlier communities

Related to the previous concern about OTUs, it would be helpful to know which two communities are the outliers in the PCAs in Fig. 5. In particular, if the two outlier fungal communities are N5 and N6 (as I suspect), it is important for the reader to know this, so that they can interpret the PCA appropriately.
Validity of the findings: - Incorrect significance calculations in Table 1

The specific example I noted in my previous comments has been changed, but the other values in the table appear to be unchanged. The authors should check all calculations in this table, since this was just an example of what seems to be a fundamental problem. As another example: pH for N in spring and winter is stated as significantly different: 5.56±0.35a and 5.33±1.14b.

Furthermore, the asterisks seem to indicate that rhizosphere and non-rhizosphere soil are different across the entire parameter, not pairwise statistical comparisons (for example, cellulase in summer: 0.47±0.04a* and 0.47±0.04a). I suspect this significance is derived from ANOVA, in which case it should not be presented for each data point. I suggest the authors instead show this significance in the soil column as R* if the rhizosphere is significantly different.

Finally, the footnote to the table in the original manuscript provided important information, but is missing from the revised manuscript.

- Causality versus correlation

The authors write in their response:

“As far as we are concerned, from the fig. 9 we have learned that pH, available P and urease activity were dominant influential factors for the soil microbial community.”

I disagree with this because “dominant influential factors” means that these are the causes and the microbial characteristics are the effects. Especially for urease activity, this is not obviously correct. One cannot determine causality from correlation, and Figure 9 presents correlations. Therefore I would recommend to soften this claim (abstract, line 28-29, 224-25) to rather use words like “associated with” which do not imply causality.

- Raw data
The authors assure that they have uploaded their sequence data to NCBI, but I can’t find other raw data in the revised submission.
Additional comments: Various positive changes have been made to the text and to the figures. There are, however, still points that I feel should be addressed to improve 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: IMPACT OF ELECTROCARDIOGRAPHIC MORPHOLOGY ON CLINICAL OUTCOMES IN PATIENTS WITH NON-ST ELEVATION MYOCARDIAL INFARCTION RECEIVING CORONARY ANGIOGRAPHY AND INTERVENTION: A RETROSPECTIVE STUDY
Review round: 1
Reviewer: 1

Output:
Basic reporting: •	The manuscript is generally well-written with appropriate use of professional English language throughout.
•	The title does not match the abstract and manuscript – the title states the population is NSTEMI patients who underwent coronary angiography. However, the rest of the manuscript says the study population is NSTEMI patients who underwent PCI.
•	The introduction is short but adequately identifies absence of contemporaneous data on ECG morphology and long-term mortality in NSTEMI patients. It is appropriately referenced.
•	The manuscript conforms to PeerJ standards.
•	Figures are relevant to the study and are well-formatted and well-presented.
•	The full raw data .csv file has been supplied.
Experimental design: •	The research question is well-defined in the introduction. It is an interesting question and it is indeed surprising that ECG morphology in NSTEMI has not been evaluated before in the PCI era.
•	The study appears to have been carried out in a rigorous and replicable manner. Ethical approval has been sought and referenced. The population studied is well-defined. However, the inclusion and exclusion criteria could be more explicitly stated. For example, patients undergoing PCI after 72 hours were excluded from the study but this has not been written in the ‘Setting and patient population’ section of the manuscript.
•	ECG definitions of ST depression and T wave inversion appear to be appropriate.
•	A number of baseline characteristics have been included in the analysis but the methods for collecting these baseline characteristics have not been included in the methods section. For example, at what point were bloods for creatinine and eGFR taken and when was baseline echocardiography done?
•	Methods section lacks detail regarding angiography and stenting procedures. What was involved in the decision making process for placing stents? Were only culprit lesions stented or were all radiographically significant stenoses treated?
•	Post-PCI management has not been outlined. Were patients treated according to current clinical guidelines? 9 months of dual antiplatelets were given but what about secondary prevention medications. Were all patients referred for cardiac rehabilitation? How was compliance?
•	Statistical methods are appropriate for the study.
Validity of the findings: •	The raw data provided is adequate and the data collection appears to have been robust.
•	There are some potentially confounding factors which have not been assessed. For example, time to angiography has not been assessed. All patients underwent PCI within 72 hours but was there a difference in outcomes in patients who underwent PCI within 24 hours compared with those who underwent PCI after 48 hours? Furthermore, bystander coronary artery disease has not been reported. The presence of any untreated bystander disease may influence long-term outcomes in these patients. Was it assessed and could it be included in the analysis?
•	The clinical importance of these results have not been adequately outlined in the discussion and conclusion sections. ST depression is independently associated with poor long-term outcomes. This is despite (presumably) optimal medical and interventional treatment as per current clinical guidelines. Can anything be done, therefore, to improve the outcomes associated with ST depression or is the association simply due to the other risk factors also associated with ST depression such as advanced chronic kidney disease and diabetes?
Additional comments: •	This retrospective observational study explores the relationship between presenting ECG morphology and long-term mortality in patients with non-ST elevation myocardial infarction (NSTEMI) undergoing percutaneous coronary intervention (PCI).  The study identifies ST depression as a significant independent risk factor for long-term mortality.
•	Whilst the idea is novel and the study is well carried-out, the paper suffers from significant confounding making interpretation of the results difficult. Although it is interesting to note that ST depression is associated with significant risk factors and poor long-term outcomes when compared with T wave inversion and non-specific ECG changes, there are a lot of confounding factors which obscure the real effect of ST depression. The effect of ST depression seen in this study may simply be due to the association of risk factors which are known to be important in long-term outcomes. Poorer outcomes may also be related to factors such as bystander disease which has not been assessed in this study.
•	In addition, there does not seem to be significant clinical applicability of these findings. How will this study change clinical management of patients with ST depression? Management of risk factors such as diabetes is already a key pillar of guideline-directed management of coronary artery disease.
•	The methodology described within the manuscript is lacking important details particularly pertaining to the PCI procedures.


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: IMPACT OF ELECTROCARDIOGRAPHIC MORPHOLOGY ON CLINICAL OUTCOMES IN PATIENTS WITH NON-ST ELEVATION MYOCARDIAL INFARCTION RECEIVING CORONARY ANGIOGRAPHY AND INTERVENTION: A RETROSPECTIVE STUDY
Review round: 1
Reviewer: 2

Output:
Basic reporting: Ideally state the number of male patients in the overall data-set as part of descriptors in the abstract.

Line 164: sentence needs rephrasing.
Line 200: can take the word 'significantly' out of the sentence.
Experimental design: Lines 87 and 107: Were patients with some ST elevation, but that did not meet STEMI criteria (and were not attributed to eg LBBB/LVH/male pattern etc) all included in the 'no significant ST-T change' group, or were patients with these kinds of ST changes excluded from this study? This may be worth clarifying.

Exclusion of patients with PCI delayed >72 hours for other aetiologies - were the patients too sick or eg kidney function too poor for angiography, or were there other diagnoses suggested as the cause for troponin rise? It might be worth explaining in more detail why these patients were excluded.

Are ACS patients treated with DAPT for 9 months rather than 12 months in local guidelines?
Validity of the findings: While not absolutely essential, it would be good to know a bit about how many patients had complete revascularisation at the index procedure presenting with NSTEMI, vs culprit only +/- staged procedures, as recent data has emerged in STEMI patients. It is noted the stent number does appear similar in all 3 groups.
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: IMPACT OF ELECTROCARDIOGRAPHIC MORPHOLOGY ON CLINICAL OUTCOMES IN PATIENTS WITH NON-ST ELEVATION MYOCARDIAL INFARCTION RECEIVING CORONARY ANGIOGRAPHY AND INTERVENTION: A RETROSPECTIVE STUDY
Review round: 2
Reviewer: 1

Output:
Basic reporting: Line 119-120 - 'Briefly, diagnostic catheterization and intervention were performed within 72 hours as possible after the diagnosis of NSTEMI was confirmed' does not make sense. Should read 'as soon as possible'?

Line 264 - should read 'A previous study....'
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The authors have satisfactorily responded to previous concerns. Specifically, I am satisfied that revascularisation strategies were largely standardized across groups and therefore unlikely to contribute to significant differences in long-term outcomes. In addition, post-PCI treatment also seems to be standardized and appropriate. The clinical applicability of these results have also been addressed 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: IMPACT OF ELECTROCARDIOGRAPHIC MORPHOLOGY ON CLINICAL OUTCOMES IN PATIENTS WITH NON-ST ELEVATION MYOCARDIAL INFARCTION RECEIVING CORONARY ANGIOGRAPHY AND INTERVENTION: A RETROSPECTIVE STUDY
Review round: 2
Reviewer: 2

Output:
Basic reporting: Thank you for making changes. As a dataset descriptor, it would still be good to know about the gender breakdown of the entire study population and state this. It can be seen that there were 77.5%, 68.1% and 65.7% males in the groups with no ST change, inverted T wave and ST depression respectively, which means the proportion of males in the total group must be in the low 70s, but I think putting this in early in the results is best. This kind of descriptor makes it easier to compare data across studies.

As a slight grammatical comment, we would usually say 'an' ST depression/decrease rather than 'a' ST depression/decrease in spoken and written English, so this could be changed where it appears in the manuscript for easier reading.

There are a few parts of the corrections that would benefit from other slight grammatical corrections, if they could be proof-read again.
Experimental design: The design is adequate for the question being asked.
Validity of the findings: Thank your for including a description of the total revascularisation vs incomplete revascularisation proportions in the overall group. It would be ideal to see if incomplete revascularisation was a predictor of the primary or secondary end-point as well, if you have this data.
Additional comments: Overall this is an improved 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: INTEGRATED ANALYSIS OF LYMPHOCYTE INFILTRATION-ASSOCIATED LNCRNA FOR OVARIAN CANCER VIA TCGA, GTEX AND GEO DATASETS
Review round: 1
Reviewer: 1

Output:
Basic reporting: As for the writing style, I recommend re-writing or re-organizing the 'results' section of the paper. In most of the paragraphs in results section, two major components are missing: rationale to conduct the experiment, and brief summary of the meaning of results. As the writing stands so far, the 'results' section is much too descriptive and contain some methodology. I suggest only showing key numbers and methods that are relevant to understanding the key findings of each section, and additional details can be relocated to the methods section or supplementary materials.

Figures and tables are cluttered with information, which prevents the main points from standing out. Therefore, I recommend condensing figures and tables, and moving some of them to supplementary materials. For example, Figure 1 can be moved to supplementary materials. Table 1 can either be moved to supplementary materials or extracted for the necessary rows/columns for the readers to understand the point being made. Figure 5 and 6 do not have to present each of these experiments - representative examples should be selected, shown, and discussed to make the key points, and other panels should be moved to supplementary materials. Figure 5 is complicated, but it was only mentioned once in the text without any mentioning of what the patterns of the figures mean.
Experimental design: The experiment performed in this paper meets the aims and scope of the PeerJ. The goal of trying to find lncRNA-miRNA-mRNA interaction axes have been well laid out in intro, although emphasizing these in results and how the overarching question is linked to each experiment will strengthen the paper. Additionally, the paper will be much stronger if the authors can provide the background of why using lncRNA as a biomarker of cancer is optimal compared to other existing techniques.

As stated above, the article will be much stronger if the authors can guide the readers through the logic in the results section of the paper. I recommend (1) add a sentence to the beginning of each paragraph laying out the reason to conduct these experiments and the hypothesis being tested or open-ended questions being asked; (2) briefly summarize the findings at the end of each paragraph.
Validity of the findings: The correlation between lncRNA expression and lymphocyte infiltration is weak. Certain panels of Figure 6 clearly show high p-value and lack of correlation. The authors focus on the ones that are correlated, but this type of 'cherry-picking' can only be done if there is clear biological meaning behind the specific pair of comparison. Otherwise, a clear reason of the pairs that do not show correlation should be given. The p-values of Figure 6 are also subject to multiple testing correction because all lncRNAs were tested against all lymphocyte infiltration markers trying to draw a conclusion of their overall correlation.
Additional comments: In this manuscript, Wu et al. profile lncRNA and miRNA in high-grade serious ovarian cancer. The authors propose several lncRNA-miRNA-mRNA axes as biomarkers of this cancer. I appreciate the large amount of work in this study including data collection and detailed analysis, but I would recommend a revision to let the main message of the paper stand out more clearly to the readers.


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 ANALYSIS OF LYMPHOCYTE INFILTRATION-ASSOCIATED LNCRNA FOR OVARIAN CANCER VIA TCGA, GTEX AND GEO DATASETS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article is written in an unqualified format, including alignment, cited location of references (Usually before periods), the use of spaces and punctuations, and the mixture of abbreviation and full name. Writing (logic and language) needs to be improved.
Experimental design: The RNA-seq datasets used in the study were downloaded from TCGA and GTEx. What is the specific form of the data (fpkm, Rpkm or TPM)? The authors need to specify this form in detail. In addition, the batch effects also need to be considered.
I am afraid these will effect the following differential analysis results (The number of differentially expressed genes is so large).
In line 153, the gene expression level is displayed with log2 transformation. The authors did not explain why this process is needed.
The validation data sets used in this paper are only used for differentially expressed analysis. Further analysis on the validation data and results comparing are not implemented.
Validity of the findings: The correlation between lncRNAs and marker genes of tumor-infiltrating lymphocytes, and the correlation between the ceRNA biomarkers and lymphocyte infiltration are very weak indeed (<0.3). So the reliability of the correlation analysis results is questionable.
Additional comments: Differentially expressed lncRNAs, miRNAs, and genes are detected that could be
positively correlated with overall survival of HGSOC. In addition , they constructed a ceRNA network, which indicated a pre-dominant involvement of the immune-related
pathways. They defined several prognostic biomarkers for the incidence and progression of HGSOC and constructed a network for ceRNA axes; among which three have a positive correlation with lymphocyte infiltration, namely; FTX-hsa-miR-150-5p-STK11, LINC00665-hsa-miR449b-5p-VAV3 and LINC00665-hsa-miR449b-5p-RRAGD.


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 ANALYSIS OF LYMPHOCYTE INFILTRATION-ASSOCIATED LNCRNA FOR OVARIAN CANCER VIA TCGA, GTEX AND GEO DATASETS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The paper focuses on a subject of interest with a design that seems correct. Reusing available data is an important area of current research.
The article is written in a correct English and is unambiguous. The state-of-the-art is sufficient and it is easy to follow what had been done.
Unfortunately, the Figures are too often difficult to read (too small and overwritten, especially Figures 2, 5 and 6), this greatly diminishes the interest of reading.
Experimental design: Research question is well defined, relevant and meaningful. The design is coherent and the analysis in depth.
On the other hand, it lacks a little critical sense. The main point is the discussion of the conservation of different genes, experiences, and the impact of these choices on the final list. This point is not discussed enough and remains critical and objectionable.
Methods are properly described with sufficient information to be reproducible. This is a very good point.
Validity of the findings: Of course, it would be easy to say (i) the data are not generated locally and above all (ii) no experimental confirmation has been made (translation = from in silico).
I would say that (i) it is therefore a good thing, we are in the era of big data and the use of available data and (ii) it is perfect it allows proposing new hypotheses that are not sometimes not even possible to test at the moment.
My critical point is the description of the choices that leads precisely to the list, the article is too descriptive and lacks criticism on these points.
Additional comments: an interesting approach, a well-conducted article, which needs a little improvement to make it excellent.


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 ANALYSIS OF LYMPHOCYTE INFILTRATION-ASSOCIATED LNCRNA FOR OVARIAN CANCER VIA TCGA, GTEX AND GEO DATASETS
Review round: 2
Reviewer: 1

Output:
Basic reporting: See "general comments".
Experimental design: See "general comments".
Validity of the findings: See "general comments".
Additional comments: Most of the major issues have been addressed in the revision. I recommend accepting 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: INTEGRATED ANALYSIS OF LYMPHOCYTE INFILTRATION-ASSOCIATED LNCRNA FOR OVARIAN CANCER VIA TCGA, GTEX AND GEO DATASETS
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors answered most of my questions.
The manuscript has been greatly improved.
Experimental design: The authors answered most of my questions.
The manuscript has been greatly improved.
Validity of the findings: The authors answered most of my questions.
The manuscript has been greatly improved.
Additional comments: The authors answered most of my questions.
The manuscript has been greatly 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: ASSOCIATION OF HEART RATE TRAJECTORIES WITH THE RISK OF ADVERSE OUTCOMES IN A COMMUNITY-BASED COHORT IN TAIWAN
Review round: 1
Reviewer: 1

Output:
Basic reporting: Overall, this is a well written manuscript. An appropriate background and context has been provided for this study.
Experimental design: Major issues:

•	Over 14 years of follow up it is likely that many participants may be started on medication that could affect the heart rate e.g. beta blockers, rate limiting calcium channel blockers. Was this taken in to account?
•	Similarly, was any consideration given to medication that could affect the heart rate at baseline e.g. inhaled corticosteroids or beta 2 agonists, anti-depressants, thyroxine?
•	Did you provide any instruction to participants about use of other products that may alter heart rate e.g. caffeine and smoking, prior to heart rate assessments occurring?
•	Were pregnant women included in your study cohort (as this may affect heart rate)?
•	How did you treat other arrhythmias and conduction disturbances identified on ECG at baseline e.g. atrial flutter, second degree AV block, first degree AV block, frequent ectopy which may affect heart rate?
•	How were individuals with arrhythmia diagnosed on ECGs during study follow up visits treated? Were they censored at this point in time?
•	How did you treat individuals with pre-existing diagnoses of cardiovascular or cerebrovascular disease? Were they included in your study population? Please outline if individuals with serious comorbidity were eligible for study participation e.g. cancer?
•	Can you please outline why you did not include eGFR and smoking as time updated covariates?
•	In your study flow chart can you please outline reasons for reduction in the study cohort at each follow up time period? It would appear that almost two thirds of your study cohort did not attend the third follow up visit, which may impact on results obtained.
•	Can you please outline how secondary outcomes were obtained? Was there a systematic search for events or was this based on participant interviews? Was there adjudication of events?
•	Were all coronary heart disease outcomes required to have an angiogram for classification? If an individual had an MI without undertaking angiography, how was this classified?

Minor issues:

•	In the abstract, please add in the corresponding 95% confidence intervals for the hazard ratios provided.
•	In your keywords it would be worth considering the addition of ‘cerebrovascular accident’, as this was a main study outcome.
•	For regular physical activity, it seems unusual that you should mandate this as two to three times per week in frequency. How were individuals who exercised with greater frequency categorised?
•	You have stated that BP measurements were taken on both arms and if there was a discrepancy of >10mmHg, then another measurement was taken. How was the final BP measurement decided in these scenarios?
•	Do you have any information concerning cause of death in the cohort?
•	In table 4 you have listed atrial fibrillation as a covariate and, in your methodology, you have stated that this patient population was excluded – please clarify if all participants with AF were excluded or if it was only those with AF at the time of the baseline ECG.
•	In Table 5 it would be clearer to state that each of the categories was compared to a stable HR trajectory in the heading or footnote as opposed to adding in ’………/stable ‘ for each trajectory, which could be misleading.
Validity of the findings: The discussion would benefit from further refining to discuss your findings and clinical implications in greater detail. It would also be useful in your discussion to refer to the approximate % change that was classified as ‘markedly increased’ to facilitate translation of your results in to clinical practice.
Additional comments: Overall, this is a clear and generally well written paper. It is lacking in methodological detail and a significant expansion of the methodology section is required.


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: ASSOCIATION OF HEART RATE TRAJECTORIES WITH THE RISK OF ADVERSE OUTCOMES IN A COMMUNITY-BASED COHORT IN TAIWAN
Review round: 1
Reviewer: 2

Output:
Basic reporting: The text is clear and the paper generally well-written. The Discussion could be more to the point, for example the "Main findings" repeat substantial parts of the Methods and also lists Limitations or Strengths. Some restructuring would be needed.

The paper by Seviiri et al, Heart, 2018 is important given the scarce literature in the field. It should be discussed in the Introduction and Discussion.

Tables should contain mre information to be read stand-alone, e.g. explain how P-values were calculated, or statistical models and adjustment variables etc.
Please also clarify: "based on the interquartile range of the final heart rate."

Table 1, 2, and 3 are all very descriptive only, it might be possible to merge or shorten them.

The Discussion should contain more comparison with a one-time point assessment, and possibility of bias due to selection of participants (necessary to create the trajectory). Maybe use Banack Am J Epidemiol 2019.

Tables should contain the number of participants and number of observed deaths.
Experimental design: Generally well analysed, with clear aims and appropriate methods.

It would be good to show a less adjusted model to know more about confounding. Less adjusted estimates may also be more clinically valid. I suggest adjusting only for age and sex in an additional crude analysis.
Validity of the findings: More description of the findings, including "non-significant" is needed.

Better acknowledgements of limitations and possible biases would be good too.

In this cohort, in fact, heart rate trajectories did not appear fo be very useful, did it?

The width of the confidence intervals given >500 death events were observed is quite surprising.
Additional comments: This is a generally wel-written and analysed paper. I encourage the authors to address my comments to improve 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: ASSOCIATION OF HEART RATE TRAJECTORIES WITH THE RISK OF ADVERSE OUTCOMES IN A COMMUNITY-BASED COHORT IN TAIWAN
Review round: 2
Reviewer: 1

Output:
Basic reporting: The background is appropriate. Overall, the manuscript would benefit from English editing to improve readability.
Experimental design: There are a number of methodological areas that require addressing to improve this manuscript:
•	In your study flow chart, please list exclusion reasons for all of the study cohort. Whilst deaths have been accounted for, other reasons for attrition require documenting. If individuals are lost to follow up, this should be clearly stated. As this represents approximately two thirds of your cohort, it is important that this is clearly articulated.
•	I’m unclear about how you have ascertained that this attrition over time did not impact on your results in this statement: ‘The decreased number of participants in the follow-up visits did not misclassify the participants much into wrong groups and influence our results.’ Whilst you may not have misclassified the remaining participants in the cohort, it is impossible to state how the results may have been affected if there had not been such a large attrition rate.
•	Please specify in the manuscript how secondary outcomes were identified, and how these events were adjudicated. This has been responded to in your initial response to my reviewer comments, but no further detail has been added into the manuscript. Furthermore, I am still unclear if systematic searching for events occurred i.e. were medical records routinely screened or did this occur only if an individual reported an event? Your methodology section should clearly state how individuals were followed up – was this by phone calls or face to face interviews? At what time intervals did follow up occur? Please also provide details for the process of adjudication of events for secondary outcomes in the manuscript.
•	For coronary heart disease, please clarify if any consideration was given to angina, or those who underwent coronary angiography with documented disease but did not undergo percutaneous coronary intervention.
•	Please document in the manuscript information that was given to participants to ensure that confounding factors that may affect heart rate were considered e.g. avoidance of caffeine, smoking etc and for how long prior to testing.
Validity of the findings: •	In your results section, it would be useful to describe the results of the four heart rate trajectory patterns with your secondary outcome (it is in Table 5 but there is no mention of this in the text).
•	In your discussion, this would benefit from explicitly stating in the opening sentences that your study demonstrated an association between heart rate trajectories and all cause mortality, but no association was evident between heart rate trajectories and cardiovascular events (secondary outcomes). It would be useful to hypothesise in your discussion about reasons underpinning this.
•	I am unclear as to the meaning of this sentence in your discussion: ‘Compared with this study, we followed our participants for years after establishing the heart rate trajectory model to demonstrate that the adverse outcomes were the cause rather than the consequence of heart rate.’ Your study has not demonstrated any causation, but rather association, so I’m unsure what this means. Please clarify and re-word.
Additional comments: Overall, this is an improved version. The limitations of the study have been described but greater detail concerning methodology is required before this could be considered 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: ASSOCIATION OF HEART RATE TRAJECTORIES WITH THE RISK OF ADVERSE OUTCOMES IN A COMMUNITY-BASED COHORT IN TAIWAN
Review round: 2
Reviewer: 2

Output:
Basic reporting: Some text has been added to the Discussion, but the English should be improved.
Experimental design: OK
Validity of the findings: OK
Additional comments: Overall my comments were addressed quite appropriately.

Some text has been added to the Discussion, but the English should be improved.


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

Input:
Title: TETRANDRINE ALLEVIATES CEREBRAL ISCHEMIA/REPERFUSION INJURY BY SUPPRESSING NLRP3 INFLAMMASOME ACTIVATION VIA SIRT-1
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1. Discussion should be added to existing relevant reports.
Eg.
[1] Zhang Juntie, Guo Ruixia, Li Xia, et al. Tetrandrine Cardioprotection in Ischemia-Reperfusion (I/R) Injury via JAK3/STAT3/Hexokinase II [J]. Eur J Pharmacol, 2017, 813(1): 153-160. DOI: 10.1016/j.ejphar.2017.08.019
Experimental design: 1. “Materials & Methods – Experimental protocols” Line 144 to 146. Please provide references on dosage and method of Tetrandrine treatment.
Validity of the findings: 1. “Materials & Methods – Experimental protocols” Line 141-143. “A total of 45 mice were randomly divided into three groups: sham operation (Sham, n = 15), MCAO treatment with vehicle (Vehicle, n = 15) or tetrandrine (MCAO+Tet, n = 15).” In Figure 1B, it was shown five brain sections in each groups, but in supplemental file “File_3._Raw_data-_Fig1.”, it was shown six brain infarct volume data in each groups! Therefore, how many mice were in each group, and why the number did not match!
2. “Materials & Methods – Intracerebroventricular injection of Sirt-1 siRNA” Line 194-203. What is the siRNA transfection method used? The method should be described more detailed. How silenced efficient of Sirt-1 siRNA in vivo., please provide experimental data.
Additional comments: Ischemic stroke is a leading cause of disability and death worldwide, which creates a heavy burden to patients and to society in the long run. Tetrandrine (TET), a bisbenzylisoquinoline alkaloid has been used for the treatment of cardiovascular diseases and hypertension. Recent studies provide the TET exerts cardioprotection in ischemia-reperfusion (I/R) injury, but the mechanisms was not well clear. In this manuscript, Dr. Wang and colleagues looked at the possible actions of the TET on cerebral ischemia and the related mechanisms involved in NLRP3. The study’s conclusion showed that TET has benefits for cerebral I/R injury partially related to suppression of NLRP3 inflammasome activation via regulating Sirt-1. Although the current study is interesting, there are some major concerns that need to be addressed before consideration of publication.

Major concerns:
1. In the 2017 published article [1], Dr. Zhang and colleagues also analyzed the mechanisms of tetrandrine exerts cardioproteciton in ischemia-reperfusion (I/R) injury, so it is necessary to discuss the similarities and differences between the two studies.
[1] Zhang Juntie, Guo Ruixia, Li Xia, et al. Tetrandrine Cardioprotection in Ischemia-Reperfusion (I/R) Injury via JAK3/STAT3/Hexokinase II [J]. Eur J Pharmacol, 2017, 813(1): 153-160. DOI: 10.1016/j.ejphar.2017.08.019
2. “Materials & Methods – Experimental protocols” Line 141-143. “A total of 45 mice were randomly divided into three groups: sham operation (Sham, n = 15), MCAO treatment with vehicle (Vehicle, n = 15) or tetrandrine (MCAO+Tet, n = 15).” In Figure 1B, it was shown five brain sections in each groups, but in supplemental file “File_3._Raw_data-_Fig1.”, it was shown six brain infarct volume data in each groups! Therefore, how many mice were in each group, and why the number did not match!
3. “Materials & Methods – Intracerebroventricular injection of Sirt-1 siRNA” Line 194-203. What is the siRNA transfection method used? The method should be described more detailed. How silenced efficient of Sirt-1 siRNA in vivo., please provide experimental data.
4. “Results – Tet inhibited the NLRP3 inflammasome-derived inflammation in cerebral I/R injury in mice” Line 245, Figure 3A to C. The western bolting should show the all samples in each group.
5. “Results – Tet inhibited the NLRP3 inflammasome-derived inflammation in cerebral I/R injury in mice” Line 245-246, Figure 3D and E, ELISA is the quantitative analysis, so the “IL-1beta and IL-18” protein levels should be shown by absolute value.
6. “Results – Tet upregulated Sirt-1 expression and suppressed NLRP3 inflammasome activation through Sirt-1” Line 256, Figure 3F and G. The western bolting should be shown the all samples in each group.
7. “Results – Tet upregulated Sirt-1 expression and suppressed NLRP3 inflammasome activation through Sirt-1” Line 257-259. “…cerebral Sirt-1 was partially knocked down by siRNA in mice.” Please provide experimental data.
8. “Results – Tet upregulated Sirt-1 expression and suppressed NLRP3 inflammasome activation through Sirt-1” Line 263-265, Figure 5. “…Sirt-1 siRNA markedly enhanced expression of the NLRP3…” Immunofluorescence data are not sufficient to support this conclusion, so western bolting should be perform same as Figure 3A to C.
9. “Results – Tet inhibited the NLRP3 inflammasome-derived inflammation in cerebral I/R injury in mice” Line 266, Figure 5B and C, the protein levels of IL-1beta and IL-18 should be shown by absolute value.

Minor comments:
1. “Materials & Methods – Experimental protocols” Line 144 to 146. Please provide references on dosage and method of Tetrandrine treatment.
2. “Results – Tet inhibited the NLRP3 inflammasome-derived inflammation in cerebral I/R injury in mice” Line 245, Figure 3A and C. “Caspase-1” should be marked by “Cleaved caspase-1”.


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: TETRANDRINE ALLEVIATES CEREBRAL ISCHEMIA/REPERFUSION INJURY BY SUPPRESSING NLRP3 INFLAMMASOME ACTIVATION VIA SIRT-1
Review round: 1
Reviewer: 2

Output:
Basic reporting: Language
1.The English writing is also necessary to be revised and polished again before it is accepted. It needs a minor revision to improve the scientific quality for publication.
Literature references
1.In the introduction section (line 95-97), the authors wrote " Tet has received extensive
   attention for its anti-tumor, anti-inflammatory, and analgesic actions". This sentence
   needs referencing.
2. Line 147-148. The authors wrote " Brains were harvested for the subsequent
   experiments (Figure 1A).". This part should belong to the results.
3. In the line 304, the authors wrote " such as anti-cancer, anti-inflammatory, and
   cytoprotective effects.". This sentence needs concrete referencing.
4. In the line 307, the authors wrote " Tet has been reported to attenuate heart, liver and
   small bowl from I/R injury.". This sentence needs concrete referencing.
Figure
1. Figure 3A is very small and of poor quality and cannot be evaluated.
2.Please explain why the expression of caspase-1 is high in the group of sham
   in Fig 3A.
3.Fig 3F is almost invisible.
4.Please supplement the relative molecular weight of all protein antibodies in Fig 3A and
   3F.
5. Fig4A the fifth piece in the group of Sirt-1 siRNA is incomplete and the third piece in the
   group of Tet+Sirt-1 siRNA is problematic.
6.In Fig 5A, NLRP3-positive cells in Iba-1-positive cells in hippocampus should be
   quantified and compared between the groups.
7. In Fig 5A, all images should be taken from the same field of view, and the author should
   offer the scale bar.
Experimental design: The author firstly demonstrated that Tetrandrine alleviates cerebral ischemia/reperfusion injury by suppressing NLRP3 inflammasome activation via Sirt-1. The idea is interesting and novel.The logic thinking of results in this article , however, needs should be considered.
1.Please illustrate the reasons selected a concentration of 30 mg/kg tetrandrine
   intraperitoneally once a day for 7 days, and supplement more data to accord with the
   choice.
2.The logic thinking of results in this article needs should be considered.
Validity of the findings: no comment
Additional comments: The author should know that the research articles must be carefully written.


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: TETRANDRINE ALLEVIATES CEREBRAL ISCHEMIA/REPERFUSION INJURY BY SUPPRESSING NLRP3 INFLAMMASOME ACTIVATION VIA SIRT-1
Review round: 1
Reviewer: 3

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: In this manuscript, the authors demonstrated that Tetrandrine(Tet) reduces cerebral I/R injury through inhibition NLRP3 inflammasome activation by upregulating Sirt-1. They established a cerebral I/R injury mice model through MCAO surgery to confirm Tet had the neuroprotective affects. Furthermore, they indicated that Tet upregulated Sirt-1 and sequentially inhibited NLRP3 inflammasome activation. This study aims to uncover the biological function and potential molecular mechanism of Tet in cerebral I/R injury. However, there are several concerns in the whole project.
1. The description “treatment of Tet could reduce the neuro- injury in MCAO model of mice” has already concluded from previous study in introduction section. So, the novelty of the whole study is not good enough at least in the first part of study.
2. The effect of Sirt-1 siRNA should be detected and shown before in vivo experiments.
3. In Materials & Methods, 45 mice were randomly divided into 3 groups to detect the function of Tet and Sirt-1 siRNA in cerebral I/R injury mice. However, the design of the animal experiments is confused as the raw data is not identical to the presented figure.
4. The authors described that Sirt-1 siRNA was injected into the right lateral ventricle. What about the control group (Tet group) in Figure 5? Scientifically, they should be carried out the same operating procedure with the solvent which was used to dilute Sirt-1 siRNA. So, the manipulations of study should be conducted rigorously.
5. In Abstract, Results section, I think the authors mean “Tet attenuated I/R-induced enhanced expression of NLRP3 inflammasome, caspase-1, IL-1β, IL-18 via upregulating Sirt-1”, not “and Sirt-1”.
6. The levels of IL-1β and IL-18 by ELISA assay were presented in relative fold change to sham group, please provided the absolute quantitative level of them in each sample.
7. The quantitative data and method of Immunofluorescence assay in Figure 2 and Figure 5 should be provided.


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: TETRANDRINE ALLEVIATES CEREBRAL ISCHEMIA/REPERFUSION INJURY BY SUPPRESSING NLRP3 INFLAMMASOME ACTIVATION VIA SIRT-1
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: Ischemic stroke is a leading cause of disability and death worldwide, which creates a heavy burden to patients and to society in the long run. Tetrandrine (TET), a bisbenzylisoquinoline alkaloid has been used for the treatment of cardiovascular diseases and hypertension. Recent studies provide the TET exerts cardioprotection in ischemia-reperfusion (I/R) injury, but the mechanisms was not well clear. In this manuscript, Dr. Wang and colleagues looked at the possible actions of the TET on cerebral ischemia and the related mechanisms involved in NLRP3. The study’s conclusion showed that TET has benefits for cerebral I/R injury partially related to suppression of NLRP3 inflammasome activation via regulating Sirt-1. The paper is significantly improved and all concerned raised by the reviewer have been addressed. I think it is suitable for publication at this point for this version of revised 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: TETRANDRINE ALLEVIATES CEREBRAL ISCHEMIA/REPERFUSION INJURY BY SUPPRESSING NLRP3 INFLAMMASOME ACTIVATION VIA SIRT-1
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: In this manuscript, Dr. Wang and colleagues demonstrated that Tetrandrine (Tet) reduces cerebral I/R injury through inhibition NLRP3 inflammasome activation by upregulating Sirt-1. They established a cerebral I/R injury mice model through MCAO surgery to confirm Tet had the neuroprotective affects. Furthermore, they indicated that Tet upregulated Sirt-1 and sequentially inhibited NLRP3 inflammasome activation. This study aims to uncover the biological function and potential molecular mechanism of Tet in cerebral I/R injury. The authors have revised the paper carefully according to the concerns raised by reviewers in the current version, and I think it is 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: PUBLIC PERSPECTIVES AND MEDIA REPORTING OF WOLF REINTRODUCTION IN COLORADO
Review round: 1
Reviewer: 1

Output:
Basic reporting: This is a very well written and organized paper. I found it very accessible and very few errors or omissions.
Experimental design: I found the research questions to be well defined and logical. My only concern relates to the size of the sample if media articles (question #4). With only 15 articles collected I found this too be too small a sample to conduct a framing analysis. I also found it a bit odd that the media articles were coded based on the findings of the survey.
Validity of the findings: Results were well integrate into the existing literature and the discussion was well written. As I mentioned above,collecting only 15 articles suggests that the reintroduction of wolves was not a salient media subject and therefore, while informative, caution should be taken when comparing to the survey results. In other words, i don't think there is enough here to conduct a comparative analysis with the survey results.
Additional comments: I feel that the number of media articles is not sufficient enough to conduct any real analysis. At the same time, I do think it is informative to situate the media coverage when discussing practical implications. I would suggest dropping question #4 but including some of the findings from the articles in your discussion/implications.


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: PUBLIC PERSPECTIVES AND MEDIA REPORTING OF WOLF REINTRODUCTION IN COLORADO
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article is written in a clear and concise language and is methodologically sound. The authors have done a credible job in surveying public opinions and analyzing media content regarding the wolf reintroduction issue.

There are a couple of important omissions with regard to references. Moreover, the way the figures are displayed can be improved. Below are my suggestions:

Abstract:

•	Add some information about your sampling and sample size, e.g., the number of respondents and representativeness of the sample.
•	Similarly, add some information about the number of newspapers analyzed and the timeframe

Introduction:

•	Line 86: One important omission is the results of the survey by Meadow et al. (2005). Please include this article in your review:
https://doi.org/10.2193/0091-7648(2005)33[154:TIOPAO]2.0.CO;2

Results:

•	L. 289: The second “responses” should be removed.
•	L. 365: “increase in tourism” instead of “increased in tourism.”
Experimental design: Materials & Methods:

•	L 141-144: Three regions are mentioned with 200 samples planned for each; however, the total sample size is 734 (L. 168). Please clarify why the sample size exceeds the planned number (3x200=600). Also, provide some information on what region classification was used (e.g., Colorado Parks and Wildlife management areas). It is important to provide this information since the study claims to survey representative, state-wide opinions.
•	L. 169-196: The use of online panels is getting more common in human dimensions of wildlife research and similar areas. The authors have done a good job of elaborating on the pros and cons of such a method of data collection. However, these two paragraphs seem to be too lengthy, given that the audience is familiar with these issues. I suggest the authors condense this content to a few sentences mentioning the main points and citations.
•	Instead of the above content about online panels, it is worthwhile to include the information regarding the “Weighting of Survey Data” in the main text, instead of the supplementary material.

Results:

•	Some of the figures 2-6 can be combined into one figure. For instance, Figures 2 and 3 can be combined. In this way, the information becomes more accessible to the reader. Moreover, the authors could free up some space and add Figure S-1 to the main text. Figure S-1 contains information that deserves being in the main text.
•	Some of the percentage values are reported with Confidence Intervals in the text and some are not. I suggest the authors be consistent in the format of reporting these values.
Validity of the findings: Discussion:

•	L. 380: Compare your results also with the results from the Meadow et al.’s survey:
https://doi.org/10.2193/0091-7648(2005)33[154:TIOPAO]2.0.CO;2
•	L. 388-389: Since value orientations were not included in this study, this conclusion should be made with caution. For instance, “It is likely that ...” or “We speculate that …”
•	L. 411-423: Briefly speculate why media coverage is more about the negative outcomes.
•	L. 454: Briefly reiterate why West Slope residents are likely to be more suspicious.
•	L. 455: Briefly add the possible bias due to collecting data through an online panel.
•	On the possible effects of media, it is worth mentioning the ‘social amplification of risk’ literature. For example, see Gore & Knuth (2009):
https://doi.org/10.2193/2008-343
Additional comments: The manuscript reports the results of a very timely survey on public support for wolf reintroduction in Colorado. This is currently a hot topic in Colorado and the United States with important implications for wildlife management and conservation. It is methodologically sound with sufficient information to be replicated. However, the authors could have done a better job by theorizing the possible drivers of public attitudes toward the wolf reintroduction. In the current format, the manuscript does not contribute to the theory, however, it has important and timely information to address policy and practice in wildlife management and conservation.