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: CAPACITY FOR HEAT ABSORPTION BY THE WINGS OF THE BUTTERFLY TIRUMALA LIMNIACE (CRAMER)
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The authors made significant improvements on their paper. However, I still have some concerns about clarity overall. Indeed, the paper provides a massive amount of data, but it is still not presented in a clear and accessible form. One critical point of the paper is to compare the thermal activity of dark and light wing portions, but this difference is not always explicitly tested. Statistical tests, including the time-series, are often based on differences before and after lighting within the same wing portion, rather than specifically comparing cumulatively “dark areas” versus all “light areas”. If the authors could frame the manuscript more clearly around this objective, the paper would read more easily. The results on single wing portions are difficult to follow, but I believe that a comparison between dark areas vs light areas as a whole, especially in the time series analysis, is needed in order to have a clear idea of the significance of the findings. Please find below more detailed comments and suggestions to improve clarity.

1. Are heat storage / non-storage and absorption / non-absorption equivalent terms? Please clarify and choose only one term and use it consistently. Also, the same areas also roughly correspond to dark and light areas, right? Please explain in the very beginning of the methods the relationship (or expected relationship) between dark/light, storage/non-storage, absorption/non-absorption and then choose one term and use it consistently for the whole paper, tables figures and figure captions.

2. Table 6 and 7 could be merged as they are the same, only for male and female. The same for table 11 and 12.

3. Please add a column specifying whether a certain area is considered or not a heat storage area. There is no way a reader will know that by heart when reading the table 10, and it makes the understanding extremely difficult.

4. Please provide what all the letters in table 10 mean. Apparently y0 is important, but there is no way of knowing what it refers to.

5. I appreciate that the authors took the time to provide statistical support for their findings and perform a time-series analysis. However, the statistical support is still missing for the “identification of heat-absorption and non-absorption areas”, only shown in figure 5. Please provide statistical testing.  Additionally, it seems that what was assessed in the time series analysis was the difference between the initial and equilibrium temperature within every single wing portion. This information is extremely redundant, and the actual use of the analysis, where all the p-values are extremely highly significant, is unclear. If the point here is only to demonstrate that the initial temperature was lower than the equilibrium temperature after lighting, the same information could have been obtained by measuring three random points on each wing. It is unclear how the authors draw their conclusions about the role of heat storage and non-storage areas, and I have a feeling that y0 is used for this purpose? What is really interesting but not tested here is the difference in the heat absorption ability (the slope of how fast heat is absorbed) of light vs dark wing areas. Indeed, when I suggested to perform a time-series analysis I meant to perform separate analyses for heat-storage and non-storage areas and then compare statistically whether they differ significantly. That is, perform a statistical model testing whether the heat absorption slope significantly differ on whether it is on a heat storage or non-heat storage area, similar to what done with the scale removal experiment. This is very relevant information.
Furthermore, it is not entirely clear how the authors conclude that the heat it transferred from one portion to the other, and how they identify how heat moves across the channels. Again, I believe this is based on the values of y0, but it cannot be understood from the text and the authors should provide more details in the methods so that the reader can understand and interpret the findings.

Minor comments:

L 15: “The scientific question remains unclear”. The scientific question is clear, but the answer remains unclear, I guess?

L16: Please include 1-2 sentences giving some background on why thus butterfly species was used to answer this question.

L15-21: This sentence is way too long and detailed for an abstract. Try to state more concisely, for example by saying “We measured a number of wing traits relevant for heat absorption including X, Y, Z” where X, Y and Z are the ones the authors found being most relevant.

L27: “Cu2, Cu3, Cu, and A in the fore wing, and veins 1A, Cu2, Cu1, Cu, M1, M3, M, R2, and R “. Again, the authors can expect no general reader to know what these symbols mean in the wing topography. This is way too much detail for an abstract and should be left out at this stage. The newly added part explaining in words what this means is clear and informative enough.

L 100-105: The fact of flying on sunny days and not on cloudy and rainy days is common to all butterfly species. What I meant by adding some background on the study organism was to explain why this particular butterfly species, Tirumala limniace, was a good model to study these questions. Is it something about the coloration of the wings, or the patterning that makes it a better model than other butterfly species occurring in the same climate? In other words, can the authors explain why this particular species was chosen instead of any another butterfly species occurring at the same latitude?
Also: replace “when on the sunny day” with “on sunny days” and “in field” with “in the field”.

L198: Please add unit of measure for thoracic temperature increase.

L293: “Sp8, Sp9, Sp10, and Sp11”: so these are dark wing portions? Please correct this in figure 9, where every portion is labelled as “light”.

L318-325: If I understood correct, what is reported in tables 10-12 is basically a comparison between the temperature of a certain wing portion at time 0 and its temperature at the final time point of the heating range, where the heating curve is fitted to have an exponential distribution? Is it so? So these data are basically summarizing what shown in figure 8, which is nice. However, I believe that the most relevant analysis for the scope of this paper is a comparison between the time series of heat storage areas and non-heat storage areas.

Also, if y is the slope, what does y0 represent? And how about A1, A2, t1, t2 and X? Please provide more details on the model variables.

L329-338: This section as it stands is not very informative. Saying that something affected something else gives no information on the direction of such effect. Please be more informative by replacing “significantly” with “positively” or “negatively”, or using phrases as “the time required to reach equilibrium temperature was shorter for X wing angles and Y light intensities”.

L340: As above. Replace “significantly” with “positively”, so that the reader does not need to go through six tables to understand the general pattern.

L384: I do not understand what expanse means. Is it the length of the wing? If so, this is a rather common characteristic in butterflies, and does not provide new information, especially in the context of heat absorption capacity. Please explain or remove (same goes for Figure 4).

Table 9: In general, the consensus for the number of * used to describe statistical significance follows the number of “zeroes” of the P-values. So that P<0.05 or 0.01 --> *, P<0.005 or 0.001 --> **. The authors chose to use *** for P<0.01 and ** for P<0.05, which is a bit confusing, but OK. However, in figure 4 they use *** for P<0.05. Please be consistent with the notation used.

L392-395: Please provide the statistical analysis and values supporting the significance of the difference in the spectral reflectance values between light and dark wing areas. Figure 5 alone is not sufficient.

L425-453: It is unclear where the results described in this section come from. As it stands now, this part is purely descriptive and lacking any statistical support. Please provide the analysis or explain where this information comes from.

Figure 9: The difference between dotted and solid lines in the figure is not clear, as they all are labelled as “light area”? Please provide more information in the figure caption or change the labels so that the figure reads clearly.

L470-472: This is nice! Is this information available also for how fast this temperature is reached (i.e. comparing slopes in the time series analysis)? Same for L487-488.

L 472-474: How can the authors be sure that Sp8-Sp11 store the heat and then transfer it to Sp7? Based on figure 9 Sp7 reaches a higher temperature and has a higher slope (? Table 10) than the other points. But I do not understand how the authors can say which areas absorb the heat and transfer it to other areas? Please explain (same for 488-491).

L489: Replace “storage” by “store”.

L515-544: It is unclear how the results about how the heat is transferred from which point to which point are obtained. For example, in L517-529: are all these data inferred from a table? Please explain your reasoning for readers not familiar with this type of data.

L583: Remove “to”

L588: Replace “branchs” with “branches”.

L609-611: This sentence is not written in correct English, please rephrase.

L699-702: How can the authors say this with certainty? Please explain reasoning in the methods.


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: CAPACITY FOR HEAT ABSORPTION BY THE WINGS OF THE BUTTERFLY TIRUMALA LIMNIACE (CRAMER)
Review round: 3
Reviewer: 1

Output:
Basic reporting: Please see "General comments for the author".
Experimental design: Please see "General comments for the author".
Validity of the findings: Please see "General comments for the author".
Additional comments: The authors made an excellent work in revising the manuscript which reads clearly now.
I only have some minor recommendations aimed at further improving the clarity of the paper. I also recommend removing any mention about the fore wing being longer than the hind wing, as it is not adding any novel piece of information (this is commonly found in butterflies), and cannot be causally linked to thermoregulatory ability in this specific study. In addition, the authors provide only weak evidence about the role of wing veins in heat transfer from heat storage areas to the base of the wing. I encourage the authors to highlight in the discussion that the role of the veins suggested is speculative. Finally, there are several points in the text which are not written in correct English grammar. I pointed out some of these below, and I recommend that the authors perform a thorough grammar check (for example with a grammar check software as “Grammarly”).

Please find detailed comments below.

L 17-23: The abstract reads much clearer now! However, this sentence is extremely long and I recommend to split it into two to enhance readability. For example, you can start a new sentence as “In addition, spectral reflectance…… were also measured”.
In addition “…scales removed or not in light or dark areas” is unclear. Consider revising.

L 23: I suggest to emphasize the results by starting at least the first sentence by “We found that…..”

L 40-41: “….courtship behavior, mating behavior, and oviposition behavior” can be simplified as “courtship, mating, and oviposition behaviorS”

L 55: “….Pieris butterflies use their PREDOMINANTLY WHITE wings….”. To emphasize the role of light wing areas in reflection rather than absorbance.

L 59: “….not only depends on reflection AND ABSORPTION…”

L 83 and elsewhere, including in the reference list at the end: The author is not “Trullas CT”, but “Clusella Trullas S”.

L 99-102: “In THE field”
“show high flight activity on sunny dayS”
I recommend a thorough grammar check with Grammarly.

L 104: “HENCE, according to the color depth….”

L 130: “…or present in light or dark areas, RESPECTIVELY”

L 133: I believe the authors should state something like “once identified the heat storage areas and non-storage areas, we also monitored real-time temperature changes in these areas…….”. Otherwise, it may sound like these areas were decided a priori.

L 147: How many? Please state sample size for males and females.

L 156: “3 days OF AGE”. Same for “4 days” and “7 days”.

L 170: Replace “where this angle” with “which”

L 274: Please add the sample size

L 287: “… evenly distributed POINTS”

L 291: This sentence should be preceded by “we defined heat absorption and heat storage areas based on the following criteria”. The definition of these areas is key to the understanding of the whole study, hence it should be stated as clearly as possible.

L 316: What does “y” represent?

L 329: Just a suggestion. There could be one final sentence stating that the direction of such results is described into detail in the following sections? So that the reader knows what to expect.

Tables 2, 3 and 4: Please specify in the caption the measurement units for temperature, time, and temperature excess.

L 367-370: Again, it is unclear what is the relevance of this finding and why it is included in this paragraph. Forewings being longer than hind wings is extremely common (if not always the case) in butterflies. I suggest removing this result as well as Figure 4.

L 390: Remove “that”

L 433-439 and 446-452: I believe there is a mathematical explanation beyond my understanding for this. However, it is a bit confusing to read about “higher rate” when the values reported in parentheses are increasingly high, but also preceded by a “-“, and therefore “more negative”? Perhaps the authors can clarify this in the methods.

L 534-535: “….requires A CERTAIN optimal wing opening angle THAT CAN VARY DEPENDING ON THE BUTTERFLY SPECIES.”

L 540-541: “In THE wild”
“need heat FOR autonomous fly”

L 545-546: I feel that this should be a fairly common finding in butterflies. Perhaps the authors could cite some other studies showing that forewings are more important that hind wings in thermoregulation?

L 553: Replace “limits” with “impacts”

L 557: Replace “Thus” with “For example, ...”

L 558-561: Again, this is generally the case in butterflies, and not specifically for this species. The authors did not formally test the causal link between variation in wing size and heat absorption and they cannot draw any conclusion about this. Forewings are also the main structure allowing flight, and their length relative to hindwings may also be motivated by that. I suggest the authors remove any statement about the fore wing being larger than the hind wing as irrelevant for the scope of this paper.

L 666-669: I am not convinced the authors have solid evidence that the veins are the mechanism underlying the heat transfer from storage areas to the base of the wing. How can the authors be certain that the heat is transferred through the vein, and not through the wing surface of a certain portion, including ALSO the vein? Perhaps this sentence should begin by “We speculate that…”.
The authors state themselves in the results that “The heat rate of the points in all veins failed to show a certain rule according to the distance from the base of the wing (Figure 9 & 10).” and again that “heat MAY mainly transfer along the veins from the points at the edge of the wing surface to the points at the base of the wing”. Hence, I would say that this sentence is indeed speculation.


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: PAIN NEUROSCIENCE EDUCATION ON YOUTUBE
Review round: 1
Reviewer: 1

Output:
Basic reporting: Thank you for the opportunity to review the article. This article is a review of YouTube on the use of pain neuroscience education videos posted on YouTube. Raw data is supplied and structure is appropriate. The intro and background support the need and build to the purpose of the study. The writing is of good quality.
Experimental design: This is an interesting topic that has not been previously looked at. The methodology to review YouTube is well explained and sound. I do have some concerns with the experimental design and the selection of the quality measurement tool. The authors do state in the limitations of the study that the tool has not been validated and that the absolute agreement between individuals was relatively low. These two limitations are very significant flaws within the design. A non-validated tool to assess quality and poor reliability with the use of the tool lead to significant concerns with any of the findings derived from the tool regarding quality of the videos. Additional concern is with potential bias of the researchers around the tool and their involvement with the Lofty Summit and creation of the seven target concepts of PNE. I recognize there may not be a better tool out there to assess quality. Nevertheless, this tool may not be ready yet for such purposes even if it is the best that is currently available. Because of the non-validation and risk for high bias around the quality assessment tool, the results and reporting of the quality of the videos based on these criteria can be construed as bias as well. In addition, the author(s) involvement with some of the YouTube videos on the list and creation of the seven target concepts was not provided in the text, this should be listed as a limitation and potential conflict of interest within the text for the reader to have full transparency of the authors and their involvement.
Validity of the findings: Significant concerns around the validity of the findings in Figure 2 in relation to the seven target concepts and the use of them for quality assessment measurement as previously stated. The authors will need to provide more significant justification on the validity of the use of these target concepts along with their bias for them and why other tools that have been validated and used were not appropriate. There is no concern with the characteristics data provided in table 1 and 2.
Additional comments: The methodology of carrying out and searching for videos within YouTube is appropriate along with the reporting of the results around the characteristics reported. The main concern is around the use of the quality assessment tool and any findings associated with this tool as previously stated.


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: PAIN NEUROSCIENCE EDUCATION ON YOUTUBE
Review round: 1
Reviewer: 2

Output:
Basic reporting: This is a well-conducted review with appropriate context, good structure and well-written. In the absence of guidelines for this type of review, you have conducted a methodologically strong review.
Experimental design: No comment
Validity of the findings: This is a well conducted review. Only one error found in the discussion of results, where table 2b should be referred to as table 2 c and table 2 c should be referred to as table 2b.
Additional comments: Well done on a challenging area to review. This is a very novel review which I think will be very useful and interesting to both clinicians and patients.


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: PAIN NEUROSCIENCE EDUCATION ON YOUTUBE
Review round: 1
Reviewer: 3

Output:
Basic reporting: -Line 72: has some harsh phrasing (most burdensome health condition facing humankind)

-On a linguistic manner: line 86: sentence is hard to follow

-The following sentences are somewhat unclear to the reader: ‘Across all videos and target concepts, the majority of the codes were ‘No, absent’, indicating that most videos did not address the target concepts of pain neuroscience education. However, there were a small number of ‘Yes, very well’ and a slightly larger number of ‘Yes, but not very well’ codes, indicating that all seven target concepts were addressed to some extent across the 106 videos.’

-You could consider to shorten the first part of the discussion between lines 363 and 464, as even though it is indeed relevant it is somewhat abundant described.
Experimental design: 1.	I found the search terms youtube to be slightly low in quantity? And could you explain how the search on one computer might have influenced the outcome?
2.	Could you explain why you did not use snowballing as well? As that would be what persons/patients naturally would do
3.	As our history influences our searches, could you explain why this was not cleared and furthermore, why you did not use an ignocnito browser?
4.	Could you explain why you had one search moment?
5.	One of the inclusion criterias is that the video is below 10 minutes, what is the reason for this?
6.	Could you explain in more detail what ‘no contradicts’ means; does the video actively state that the specific concept of pain education is not true?
7.	Did you address the quality of the videos in terms of sound/picture quality/clearness of voice/english/etc.?
8.	One of the issues I have is with the many different reviewers you used in the content coding, how did you ensure you all had the same vision/quality?
9.	Why the use of an absolute agreement level instead of Cohen’s Kappa for agreement?
10.	Furthermore, I wonder what your Engagement criteria where?
Validity of the findings: Corresponds with 2.
Additional comments: First of all I would like to thank you for your contribution to the field of Pain Neuroscience Education. With this extensive research you have highlighted an important consequence of the popularity of PNE, namely the translation of institutes and (semi)professionals of PNE into videos.

Furthermore, you have written an academic article that is clear and readable for our fellow healthcare professionals working with patients with chronic pain.

However, prior to publishing it, I would like to offer you some suggestions for improvement as listed below.


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: PAIN NEUROSCIENCE EDUCATION ON YOUTUBE
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment. Authors made necessary changes and addressed concerns from initial review.
Experimental design: No comment. Authors made necessary changes and addressed concerns from initial review.
Validity of the findings: No comment. Authors made necessary changes and addressed concerns from initial review by further addressing limitation of reliability of target concepts.
Additional comments: Authors made necessary changes and addressed concerns from initial review. Thank you for your contribution.


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 TRANSCRIPTOMIC RESPONSE TO A SHORT DAY TO LONG DAY SHIFT IN LEAVES OF THE REFERENCE LEGUME MEDICAGO TRUNCATULA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper describing a brief overview of the changes in the M. truncatula leaf tissue transcriptome following a shift of vernalised plants is well-written and presented study. It is a well written paper with minor typos .
Experimental design: The experimental designs are presented well with justification and analysis of each finding given with the paper.
Validity of the findings: The tables, and figures are documented well to justify the experimental design and results. It was a nice study and results to read. The authors can possibly combine the result and discussion part to make it robust or expand the discussion slightly as the result section contains parts from discussion.
Additional comments: No additional comments


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

Input:
Title: THE TRANSCRIPTOMIC RESPONSE TO A SHORT DAY TO LONG DAY SHIFT IN LEAVES OF THE REFERENCE LEGUME MEDICAGO TRUNCATULA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The study is well written overall and the results are clearly presented.
Experimental design: The authors have performed a straightforward transcripomic analysis of plants moved from SD to LD. The only slightly confusing aspect is that they have combined two different shift experiments on plants of different ages into one analysis, but they appear to have controlled for this.
Validity of the findings: The findings appear reasonable. The authors confirm induction of known flowering genes, suggesting that the experiment has worked and the results are meaningful.
Additional comments: The transcriptomic response to a short day to long day shift in leaves of the reference legume Medicago truncatula

In this study, Thomson et al investigate the response of Medicago leaves to inductive long days using an RNA-seq approach. In two experiments, Medicago plants are shifted from SD to LD conditions, and the transcriptome assayed at ZT0, 2 and 4 h.

The authors analyse the transcriptome data bioinformatically to determine if they can identify transcriptional responses likely to be indicative of the pathway that controls flowering in Medicago. While FT has been identified to be conserved in Medicago, the pathways controlling the induction of flowering in Medicago are much less well understood. This is an interesting study, and the authors have done a sound job of carrying out the experiments. The following are some suggestions for the study:

(1)	Line 247 discusses the difficulty of knowing which timepoint is most relevant to the regulation of FT-like genes. Did the authors consider using the expression of FT as a marker for co-expression. A transcriptional positive regulator of FT that itself is transcriptionally regulated would then be expected to have the same pattern of expression of FT. This might be a straightforward way to identify candidate FT regulators. (this is analogous to the clustering used in Fig 4b, but more direct, the authors might consider this to be sufficient for this purpose.)
(2)	An implicit assumption of the analysis and discussion is that the regulator of FT-like genes in Medicago is transcriptionally regulated. In this way, the authors find some interesting candidate TFs that are co-expressed with FT, and are thus good candidates. Another possibility is that the regulator of FT expression is post-translationally regulated. The authors should mention this specifically in the discussion, because it is important to bear in mind when considering the conclusions.
(3)	The experimental setup is not completely clear. For the plants grown in SD, at what ZT time where they shifted to LD? How many hours/days were they grown in LD before the next sampling? It seems that the LD shifted plants were sampled after exposure to a single LD (or shortened night), is this correct? (Is it known for example if a single LD is sufficient to induce flowering in Medicago? The plant may have a more robust photoperiodic response if it is entrained for several days in LD. In any case it would be helpful to discuss this)

Minor:
Line 367: “more than >2-fold” is redundant.


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 TRANSCRIPTOMIC RESPONSE TO A SHORT DAY TO LONG DAY SHIFT IN LEAVES OF THE REFERENCE LEGUME MEDICAGO TRUNCATULA
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript is well written in standard English with sufficient background information provided. The presentation and display are of high quality.
Experimental design: The research falls in the scope of the journal and the focused question is well defined and meaningful. Methods are thoroughly described.
Validity of the findings: The conclusion is well supported by the data presented and the data are statistically sound.
Additional comments: The manuscript submitted by Geoffrey Thomson et al. systematically explored the transcriptomic datasets associated with photoperiodic flowering when Medicago truncatula plants are shifted from short day (SD) to long day (LD). Though flowering has been studied extensively in the model plant species Arabidopsis, legume species seem to have some unique mechanisms that diverge from Arabidopsis. It is worth deciphering the details of these mechanisms. As a model legume, M. truncatula is an ideal material for molecular mechanistic investigation in photoperiodic flowering. Overall, the submitted manuscript sets up a solid foundation for future studies by systematically analyzing the transcriptomic data during the SD to LD shift. The manuscript is well written and the experiments were well designed. I only spotted a few typos to be changed:
Line 56, “suggest” should be “suggests”;
Line 98, delete “it” in “M. truncatula it is”;
Line 132, delete one “was” in “Soil was was kept”;
Line 145, change “was” to “were”;
Line 147, change “prepared” to “were prepared”;
Line 156, change “is run” to “was run”;
Line 202, change “is of a high” to “are of a high”;
Line 248, change “genes abundances” to “gene abundances”;
Line 292, delete “genes” in the phrase “criteria genes at at least”;
Line 301, change “strikingly” to “striking”;
Line 383, delete “are”;
Line 385, change “a ovate” to “an ovate”;
Line 400, change “were” to “are”;
Line 403, change “code” to “encode”;
Line 424, change “is ” to “are”;
Line 433, change “consists” to “consist”.


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 TRANSCRIPTOMIC RESPONSE TO A SHORT DAY TO LONG DAY SHIFT IN LEAVES OF THE REFERENCE LEGUME MEDICAGO TRUNCATULA
Review round: 1
Reviewer: 4

Output:
Basic reporting: My first comment pertains to the paragraph starting line 53 of the introduction. I think this paragraph emphasizes well the difference between the universality of FT-dependent regulation in flowering plants, contrasted against the pathways to which FT expression is coupled. While I think this is a fascinating evolutionary question, I feel it could be phrased more succinctly, and it is a number of paragraphs until you make the point that in Medicago, CO-dependent regulation of FT is not used.  I would considering re-ordering this paragraph or moving segments of it to the later paragraph to better hone in on this point. For instance, as a suggestion, you might use this to say CO-dependent regulation is a common regulatory mechanism in species X,Y,Z which could be a convergent coupling to FT regulation, but is not universal, and cite a few extra examples.  Because the paper is partially framed around helping find the mystery MtFt1a regulator, I think special care in these two paragraphs will help frame the central biological question better.

Small points:

Figure 2A: Left most panel, right side has been cut off slightly

Figure 3: Please list what PCA1,2 are in the figure legend (sampling time and photoperiod)

Two small typos on lines 382 and 283.
Experimental design: Most of my comments on experimental design relate to time point choice and time point utility using the approach outlined in this study by the authors:

	Paragraph beginning line 196/ also final paragraph of introduction line 118: While I think the authors are very clear throughout in their experimental methods, I would really like to see a more detailed discussion in either section as to why the time-points ZT0,2, and 4 were chosen (This is mentioned in the abstract, and I’d like to see it again in the results/ or at the end of the intro in greater detail).  While these time-points seem sufficient for capturing upregulation of MtFTa1 expression after LD treatment, and coincides with the initial peak of the MtFTb genes under LD, and probably similar co-expressed genes, I was curious as to why a more dispersed time series was not investigated (i.e. 0, 4, 8, for example which would capture MtFTb morning peak and trough), and I think that the author’s commentary on time point choice would be valuable for future readers who are planning a similar analysis.

	Similarly, I think this study hinges on its utility of being able to identify co-expressed transcripts with similar diurnal and photoperiodic behavior to MtFTa1/ MtFTb. While I completely agree that the authors’ analysis captures sufficiently the expression of photoperiodic genes over the time points used, as highlighted in Figure 1, I was curious if the span of time-points and kinetics for genes in this cluster are able to predict behavior at other times in the day in any meaningful way (especially for the particularly unique expression of MtFT1a). If RNA/cDNA is still available from the time courses in Figure 1, I think it might be helpful to add expression data from a couple transcripts from cluster 1 (LD/SD time-course) into the supplement, as a proof of concept (even though they are perhaps not involved in the transition to flowering). This might include Medtr1g099440, Medtr6g086805, the IRON MAN (IMA) transcripts, or Medtr4g009110.
	If the authors think the clustering analysis over their time-points is not predictive in this way, it might be useful to add a short segment about this in the discussion, and how one might design a future study to capture co-expressing transcripts for a given photoperiodic gene of interest. I think this would be of utility for others who are interested in using this approach.
Validity of the findings: In my own experience, the primary draw back of utilizing a co-expression approach for finding, for instance, an MtFT1a regulator, is that one could imagine a constitutively expressed factor whose activity is temporally regulated by light, either through interaction with a photoreceptor/photoreceptor coupled pathway or through light dependent protein level degradation.  In either case, you potentially might not be able identify the regulator using this approach. Perhaps if the regulator activated or repressed several other genes at the same level of MtFT1a, for instance, then one may have enough information to investigate candidates based on shared promoter regulatory elements, etc. Considering that these light/protein dependent mechanisms are common in photoperiodic and circadian regulatory networks, I think it is worth discussing this drawback of using the above approach briefly in the beginning of the discussion.
Additional comments: The effective use of RNA-seq data sets to the study of photoperiodic pathways poses some unique challenges in comparison to more linear signaling pathways, and this study provides a great resource to help tackle some of those challenges. I commend the authors on a very well written and assembled study, and think that it will provide a great resource for others studying photoperiodic flowering, as well as seasonally regulated pathways that are less intensively studied compared to flowering induction.


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

Input:
Title: IDENTIFICATION OF KEY GENES, PATHWAYS AND POTENTIAL THERAPEUTIC AGENTS FOR LIVER FIBROSIS USING AN INTEGRATED BIOINFORMATICS ANALYSIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is clear and unambiguous. Professional English is used throughout.

Sufficient literature is cited.

The article structure, figures, and tables have a professionally drafted.

The manuscript is self-contained with relevant results to a hypothesis.
Experimental design: The experimental design is within the aims and scope of the journal.

The research question is well defined and straightforward.

A thorough investigation is performed.

The methods are satisfactorily described with sufficient detail.
Validity of the findings: The study impactful with novel implications.

The data provided is robust and statistically sound.

The conclusion is well stated and well linked with the original research question.
Additional comments: The authors have used bioinformatics analysis to identify gene, pathways and drugs involved in liver fibrosis. However, the manuscript can only be accepted for publication after clarification of following points.
1.	CcnE2 is significantly upregulated in the HBV dataset. Please mention at what state of cell cycle CcnE2 is present and expressed? What are the potential inhibitors for CcnE2? Also what is the primary function of CcnE2?
2.	What is the molecular structure of Zosuquidar?
3.	How the Zosuquidar interacts with ABCB1? Please elaborate briefly?
4.	Only three datasets are been chosen for the study based on the rationale of fibrosis of a different etiology. Are there more datasets like these are available? If yes, what is the main reason of choosing only these datasets? Please elaborate.
5.	Figure 4, please clarify the gene marked genes in the figure legends.


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

Input:
Title: IDENTIFICATION OF KEY GENES, PATHWAYS AND POTENTIAL THERAPEUTIC AGENTS FOR LIVER FIBROSIS USING AN INTEGRATED BIOINFORMATICS ANALYSIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: In this work, the authors used bioinformatics tools to analyze three gene expression profiles of liver fibrosis from GEO database and identified key genes in the process along with therapeutic agents that may have antifibrotic activity.

The manuscript lacks on sufficient background information and literature references as noted in general comments.
Experimental design: The aim of the study is well-defined and the methods used are appropriate.
Validity of the findings: Conclusions are well stated and supported by the results shown.
Additional comments: 1)	Introduction needs improvement and should be rewritten as sufficient background covering previous bioinformatics work is not provided to understand the significance of the work. For example, lines 78-81, “However, these approaches have been limited in their ability to identify the key genes regulating the disease as a whole. Moreover, the results of these studies are often inconsistent due to different etiologies of liver fibrosis”. Authors should provide information on key genes identified in previous studies, and in the discussion section, elaborate on the similarities/differences in the hub genes identified in this manuscript to those already reported in literature.
2)	On lines 222-224, authors suggest that the 25 hub genes could be potential drug targets for antifibrotic activity. However, none of the hub genes seems to be targeted by the top 10 identified compounds (reported in Table 4) that authors suggest could be potential antifibrotic therapeutic agents. How do authors reconcile this difference?
3)	On lines 274-275, “…with CcnE2 being significantly up-regulated only in this HBV dataset, but not in the HCV or NAFLD datasets”. This statement is not supported by the data shown in the manuscript.
4)	On lines 285-286, “…the degree of inflammation is typically less severe than that caused by HBV/HCV according to our results”. It is not clear how the results in the paper relate to degree of inflammation. Can the authors elaborate on this?
5)	On lines 292-293, “but the other agents targeting similar molecules have the potential to ameliorate liver fibrosis”. It is not clear what “other agents” or “similar molecules” the authors are referring to here.
6)	Supplementary data 2-4 have been shared for review but have not been referenced in the paper anywhere.


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

Input:
Title: IDENTIFICATION OF KEY GENES, PATHWAYS AND POTENTIAL THERAPEUTIC AGENTS FOR LIVER FIBROSIS USING AN INTEGRATED BIOINFORMATICS ANALYSIS
Review round: 2
Reviewer: 1

Output:
Basic reporting: No Comments.
Experimental design: No comments.
Validity of the findings: No comments.
Additional comments: The authors have done the recommended changes and modifications in the newer version of the manuscript. Considering these change I now can recommend the manuscript for publication.


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

Input:
Title: IDENTIFICATION OF KEY GENES, PATHWAYS AND POTENTIAL THERAPEUTIC AGENTS FOR LIVER FIBROSIS USING AN INTEGRATED BIOINFORMATICS ANALYSIS
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Authors have addressed all my concerns and the manuscript is now suitable for publication.


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

Input:
Title: OCEANOGRAPHIC MOORINGS AS YEAR-ROUND LABORATORIES FOR INVESTIGATING GROWTH PERFORMANCE AND SETTLEMENT DYNAMICS IN THE ANTARCTIC SCALLOP ADAMUSSIUM COLBECKI (E. A. SMITH, 1902)
Review round: 1
Reviewer: 1

Output:
Basic reporting: Please see attached
Experimental design: Please see attached
Validity of the findings: Please see attached
Additional comments: Please see attached


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

Input:
Title: OCEANOGRAPHIC MOORINGS AS YEAR-ROUND LABORATORIES FOR INVESTIGATING GROWTH PERFORMANCE AND SETTLEMENT DYNAMICS IN THE ANTARCTIC SCALLOP ADAMUSSIUM COLBECKI (E. A. SMITH, 1902)
Review round: 1
Reviewer: 2

Output:
Basic reporting: Comments bundled in attached pdf.
Experimental design: Comments bundled in attached pdf.
Validity of the findings: Comments bundled in attached pdf.
Additional comments: Comments bundled in attached pdf.


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

Input:
Title: OCEANOGRAPHIC MOORINGS AS YEAR-ROUND LABORATORIES FOR INVESTIGATING GROWTH PERFORMANCE AND SETTLEMENT DYNAMICS IN THE ANTARCTIC SCALLOP ADAMUSSIUM COLBECKI (E. A. SMITH, 1902)
Review round: 2
Reviewer: 1

Output:
Basic reporting: No additional comment
Experimental design: No additional comment
Validity of the findings: No additional comment
Additional comments: I am satisfied with the revisions based on the prior review. This manuscript is good to go in my opinion.


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: COMPARATIVE ANALYSIS OF THE LIVER TRANSCRIPTOME IN THE RED-EARED SLIDER TRACHEMYS SCRIPTA ELEGANS UNDER CHRONIC SALINITY STRESS
Review round: 1
Reviewer: 1

Output:
Basic reporting: This study uses new laboratory methods (radseq, qpcr) and analyses (GO analysis, KEGG analysis) to try to understand the molecular pathway of salinity adaptation in a highly invasive species Trachemy scripta elegans. The paper is well written, but would benefit from some clarification in some areas. I have attached a pdf file with edits and suggestions. The literature references, as well as background provided are sufficient. I highlight a key point below:
- for the keywords, try to avoid using words that are in the title, as the title is also used as keywords in online searches. I have added some keywords that I think are appropriate.
Experimental design: This research is original and within the aims and scope of the journal. The research question is well defined and relevant to studying the cellular reaction to salinity stress, as well as invasive species. We know that T. s. elegans can live in saline habitats, and this study begins to answer the “how” question. One clarification that is needed on the experimental design:
- For methods, it is a bit confusing how many individuals were used in the study. 9 total or 18 total? This is a key point that needs to be clarified
Validity of the findings: The discussion, overall its good, but could improve. The biggest thing I thought was missing was the "why is this important?" question. You did a good job describing the results, but I think you could take it a step further. First is the identification of the key genes in TSE. After listing these genes, what next? One thing you can emphasize more are the comparisions. 0 vs 5, 0 vs 15. The genes that are shared between these comparisons are interesting--these shared pathways indicate some importance to salinity stress. Also, are there any big changes from 5 vs 15? you touched on this with the discussion of hormesis, but could be elaborated. After this, you can compare your study to the study of other studies of salinity stress. You did a good job of this, but could be elaborated a bit more. Any other studies of salinity stress that sequenced transcriptomes? Anything else you can add when comparing to the diamondback terrapin? This is a good comparison since it is also a turtle. Lastly, what are the implications of your work to understanding the invasive nature of this species? Does this help us with controlling the species? Does it indicate anything we should be careful of? This would be a nice thing to add towards the end, increase the usefulness of your study.
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: COMPARATIVE ANALYSIS OF THE LIVER TRANSCRIPTOME IN THE RED-EARED SLIDER TRACHEMYS SCRIPTA ELEGANS UNDER CHRONIC SALINITY STRESS
Review round: 1
Reviewer: 2

Output:
Basic reporting: BASIC REPORTING
1) Clear, unambiguous, professional English language used throughout
This manuscript is exceptional in its use of well-crafted English sentences. It was easy to read in that respect.
2) Intro & background

The authors lay the foundation for this report as follows. The fresh water red eared slider turtle is an invasive species whose success is due, at least in part, to its ability to invade saline environments. They state there are really two ways to deal with changing salinity (Line 63) “tolerance of elevated inorganic ion concentrations (mainly sodium and chloride) in plasma (Gordon & Tucker 1965), and accumulation of organic osmolytes (e.g. urea) to counteract cell-volume changes”. First, I would say that, as written, these are not two things, but one: tolerance could be achieved by accumulation of organic osmolytes to keep cell volumes the same.

But the two strategies are actually 1) keeping plasma osmolarity constant and 2) altering cell osmolarity to match plasma osmolarity to maintain cell volume. While it is possible that this turtle allows plasma chloride to change and responds by synthesizing organic osmolytes, the authors have previously reported increase in urine osmolarity and drop in aldosterone, consistent with the hypothesis that ability to tolerate higher salt in the environment is also achieved by homeostatic responses that act to maintain serum osmolarity at a constant level. This is what sea turtles do, and this strikes me as much more germane to this species than what crabs do. Routes of excretion should be discussed.

Commitment to exploring this particular strategy can then be put in context of their 2014 paper which also suggests that tolerance strategies are involved. The authors need to establish that they were looking for

3) Structure conforms to PeerJ standards, discipline norm, or improved for clarity.

The structure was very good.

4) Figures are relevant, high quality, well labelled & described.

The paper was very well written, and I got to the end of the manuscript without noticing the figures. Only one figure – figure 4 – is mentioned in the text of the manuscript. If figures are not mentioned in the text, they obviously add nothing to the manuscript and should be removed.

 Figure 1 does show that differential gene expression occurs. The colors used in Figure 1 are mostly a distraction, as they map directly to the x and y scales.

I recommend a Venn diagram showing overlap between significant responses at the two salinities.

Figure 2 seems to show that genes differentially expressed genes map to many categories that have no specific  connection to this experiment or the hypothesis that this turtle responds to salinity stress by increasing synthesis of organic osmolytes.

Figure 3 needs to be discussed. Why did the authors pick genes at random? If this paper is about synthesis of osmolytes in the liver in response to salt stress, the authors should do qPCR on the genes they believe are induced or repressed that explain the tolerant phenotype, rather than showing that RNA-seq works, whichis well accepted.

Figure 4 is highly speculative and highly flawed, in my view. On what basis do the authors conclude that “hormonal system” (whatever that is) drives the osmotic stress response in this turtle leading to “plasma osmotic pressure”? This appears to be a reference to their previous work showing changes in aldosterone. To make a figure like this work, they will need to create a pathway of related genes that are significantly differentially expressed, that are known to be co-regulated. For example, a transcription factor might be known to induce the expression of some gene that is part of a signaling pathway that eventually leads to increase synthesis of a particular osmolyte. The figure needs to show the direction of observed regulation and arrows showing how that gene is predicted to influence the expression of other genes in their pathway. Since this a gene expression study, there is no room here for vague concepts like “energizer”. All genes have been measured. Show how the genes work together to achieve the phenotype.

5) Raw data supplied (see PeerJ policy).

I was not able to access any raw data.
Experimental design: 1) Original primary research within Scope of the journal.

Yes.

2) Research question well defined, relevant & meaningful. It is stated how the research fills an identified knowledge gap.

The authors set out to explore the molecular basis of salinity tolerance in this turtle and found some genes that are differentially expressed that support a pre-existing hypothesis, namely, that this organism tolerates high salinity because it synthesizes osmolytes that protect it from cell volume changes. Unfortunately, it’s really just an exploration of various changes that occur, most of which have nothing at all to do with their hypothesis. I see that as more a strength than a weakness, but I would like the authors to clarify that they saw many exciting differences in the liver, suggesting a huge response, and that some of the gene expression changes are consistent with their previous hypothesis, though many are not directly related in an obvious way.

What are the key genes that responded in a way consistent with their hypothesis? I’d like a graph showing how they responded (e,g. fold change) comparing 0, 5 and 15 psu gene expression, with error bars, or the raw data points.

3) Rigorous investigation performed to a high technical & ethical standard.

Ethical standards met. Given that they performed an experiment with two levels of osmotic challenge, why comparisons between them not addressed?

4) Methods described with sufficient detail

I would like clarification on the following technical issues:

-	Why was the liver chosen?
-	Why was beta actin chosen as a reference gene (was it differentially expressed?)
-	Why was a fold change of 2 and an FDR of 0.05 chosen?
-	How was significance established in GO term and KEGG pathway enrichment?
-	Were these GO term and KEGG pathway enrichment p values corrected for multiple hypotheses?
-	How many reads were in each of the samples? Were the library sizes the same across all samples?
-	What does it mean for the transcriptomic assembly to result in 200,000 unigenes? How does this compare to your expectations?
Validity of the findings: This paper begins with a core hypothesis that needs to be stated. I believe that hypothesis is that gene expression patterns in the liver would demonstrate a response to salinity consistent with tolerance achieved by increased osmolyte synthesis. I do not believe the authors have provided persuasive evidence of this, but I think a careful cherry-picking of the data can make this a plausible argument.

Alternatively, the authors can simply characterize this an early exploration of this response. This is useful work to this field and it’s very hard to use gene expression alone to establish molecular mechanisms. In my opinion, recognizing the limitations of their design would make their new hypotheses based on gene expression more compelling, not less. But I’d like more detail about what genes they believe are driving this, based only on gene expression differences they measured here.

Finally, I’d like the authors to speculate about how their results inform the invasive species problem they lay out in their introduction. They know more (we hope) now what do we do?
Additional comments: Good luck. I think this is good work and should get into print.


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

Input:
Title: COMPARATIVE ANALYSIS OF THE LIVER TRANSCRIPTOME IN THE RED-EARED SLIDER TRACHEMYS SCRIPTA ELEGANS UNDER CHRONIC SALINITY STRESS
Review round: 2
Reviewer: 1

Output:
Basic reporting: good
Experimental design: good
Validity of the findings: good
Additional comments: I am  happy with the modifications made by the authors. One thing to be careful of is the formatting in the paper. There needs to be consistency.

For example, when making a list, do you include a comma before the "and"? It seemed that you did this more often than not, so I tried to add the comma whenever missing, but please read through the manuscript to make sure it is consistent throughout the paper.

Also, the formatting of your numbers is inconsistent. For example, are numbers written
1) 1,234
2) 1 234
3) 1234
This may be something that the editor can decide for you based on journal formatting. Make sure it is consistent throughout.

I have re-read and tried to clean up the language. I attached the manuscript with track 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: COMPARATIVE ANALYSIS OF THE LIVER TRANSCRIPTOME IN THE RED-EARED SLIDER TRACHEMYS SCRIPTA ELEGANS UNDER CHRONIC SALINITY STRESS
Review round: 2
Reviewer: 2

Output:
Basic reporting: Are Raw data supplied ?

Data are now available in GEO. Although the text in the manuscript indicates that nine turtles were used, suggesting n=3 per group, only 3 samples (total) are stored in GEO. This simple fact explains much of what needs to be changed in the manuscript. Although it is hard to do statistics with 3 replicates per group, few would agree that one can do statistics with n=1 per group.

	It is vital that the manuscript clearly state that there were no replicate measurements.
In addition, though the data cached in GEO does include count tables, which is helpful in principle. However, it is not possible to map identifiers in the count tables to anything mentioned in the manuscript. Therefore, the count tables are not useful. Information should be supplied to allow other scientists to use these data without having to perform a new de novo alignment.

Are Figures relevant, high quality, well labelled & described?

The figures collectively illustrate the following story. 1) Similar differences were observed between 0-5, 0-15, and 5-15 ppt. 2) About 30 KEGG pathways had differentially expressed genes in them. 3) Fold changes based on qPCR and RNA-seq are strongly correlated. 4) It is possible to construct a diagram using carefully selected genes that supports a (supposedly causal) relationship starting with “response to salt water” and ending with “plasma osmotic pressure.”

Figure 1 is blurry. It obviously has no relevance, because it is not mentioned in the text. However, it does raise several important questions. How were the FDR corrected p-values garishly highlighted in this figure actually calculated in an n of 1 experiment? Given the very large number of “highly significant” genes identified in each comparison, were the same genes significant in each comparison? Were genes that were significant in multiple comparisons differentially expressed in the same direction in different conditions relative to control?  Were the same or different GO groups and KEGG pathways enriched at 5 and 15 ppt? Is a dose response evident? Is the 15ppt challenge suggest that the turtles are more stressed than at 5 ppt?

Figure 2 is meaningless without indicating the fraction of genes induced and repressed. If 100% of genes associated with a particular pathway are induced in 5 ppt compared to 0 ppt, one can infer that the pathway as a whole is activated at this concentration. On the other hand, if half of the genes in the pathway are up and half are down, it is hard to know how the organism is responding. As mentioned above, this figure should compare and contrast 0-5, 0-15, and 5-15 ppt.
	This figure needs to be broken into three panels, one for each contrast in Figure 1, and the number of induced and repressed genes indicated.

Figure 3 Supports the conclusion that RNA-seq works, which would have been relevant many years ago, but is no longer in doubt. Contemporary RNA-seq papers do not waste space demonstrating that RNA-seq and qPCR yield similar results. The point of RNA-seq verification is to demonstrate that the genes central to the interpretation chosen by the authors (e.g. those in Figure 4) that were observed in a high dimension experiment (RNA-seq) can be replicated in a low dimension experiment. Randomly selected genes are irrelevant.

Here is a recent paper illustrating the use of qPCR validation and a mechanism and how Figure 2 should show fraction of induced and repressed genes : https://doi.org/10.1016/j.jhazmat.2018.11.101

	Figure 3 must be replaced by a new figure showing the genes selected in Figure 4. Each replicate turtle must be used (n = 3) and statistics performed.

Data is robust, statistically sound, & controlled.

The manuscript suggests that 9 turtles were used, in three experimental groups (0, 5, 15) and that statistics were performed using edgeR, yielding roughly 3,000 genes achieving an FDR < 0.05 and an absolute log2 fold change of 1 or more. In fact, only 1 replicate has been used. Although a kind of statistic can be generated by edgeR, it is specifically not recommended by the authors. The following is from the edgeR manual:

2.11 What to do if you have no replicates
edgeR is primarily intended for use with data including biological replication. Nevertheless, RNA- Seq and ChIP-Seq are still expensive technologies, so it sometimes happens that only one library can be created for each treatment condition. In these cases there are no replicate libraries from which to estimate biological variability. In this situation, the data analyst is faced with the following choices, none of which are ideal. We do not recommend any of these choices as a satisfactory alternative for biological replication. Rather, they are the best that can be done at the analysis stage, and options 2–4 may be better than assuming that biological variability is absent.
1.	Be satisfied with a descriptive analysis, that might include an MDS plot and an analysis of fold changes. Do not attempt a significance analysis. This may be the best advice.

	If the authors are using one of the mechanisms defined in the user guide (but not recommended) to overcome lack of replication, they must be completely candid about this or characterize the analysis as descriptive.
Experimental design: No Comment
Validity of the findings: Impact and Validity of Findings

The findings presented in this paper have not been adequately supported by the data, statistics and figures. Aside from the issues raised above, the manuscript presents itself as exploring how an invasive species invades by improved salinity acclimation.

“The [sic] physiological research has shown that T. s. elegans could increase blood
osmotic pressure by balancing the entry of NaCl with the decreased secretion of aldosterone, and accumulating urea and free amino acids in blood (Hong et al. 2014). Results of GO enrichment analysis in the study showed that ion binding, ion transmembrance transport, hydrogen ion transmembrane transporter activity, hydrogen ion transmembrane transport, hormone activity, monovalent inorganic cation transport, anion binding, and ion transport were significantly differentiated, which provide a strong evidence for the physiological mechanism. “

Which physiological mechanism? In the foregoing passage it sounds as though ion transport in the liver might be expected to play a role in salinity acclimation.  How are they proposing this might work?

If the idea is that acclimation is accompanied by changes in the urea cycle, mentioned more than once in the manuscript, it follows that many genes associated with this pathway would be induced at high salinities. As this was not reported, I assume it was not observed.
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: COMPARATIVE ANALYSIS OF THE LIVER TRANSCRIPTOME IN THE RED-EARED SLIDER TRACHEMYS SCRIPTA ELEGANS UNDER CHRONIC SALINITY STRESS
Review round: 3
Reviewer: 1

Output:
Basic reporting: No further comments.
Experimental design: No further comments.
Validity of the findings: No further comments.
Additional comments: Thanks for your hard work.


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: SPATIAL NEAR FUTURE MODELING OF LAND USE AND LAND COVER CHANGES IN THE TEMPERATE FORESTS OF MEXICO
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript titled “Spatial near future modeling of land use and land cover changes in the temperate forests of Mexico” aims to present hypothetical scenarios based on spatial modeling. While this study does not present a new approach as claimed in the conclusion section (line 379), it can still provide some useful information that are particularly relevant for local/state-level policymakers.  In my opinion this study can use a stronger study design, and a thorough editorial check for improving the language. The manuscript is full of typographical errors (see examples below) and lacks important details in methods. Please see my detailed comments below.

Abstract:
1.	The authors might consider starting this section with the big question/study rationale.
2.	There is no mention of the study area/country here which should be included in the revised version.
3.	Last sentence: ‘on’ is missing after ‘Based’.

Introduction:
1.	The flow between the paragraphs are not evident. The first paragraph talks about forest ecosystems and drivers of deforestation (while not including the wealth of literature on these topics – a serious weakness in the manuscript), and the second paragraph jumps right into Mexico and temperate forests. There should be a couple of transitional sentences that describe importance and current state of temperate forest worldwide, and then Mexico.
2.	Subsequent paragraphs discuss other studies that have created similar scenarios in other regions (again, supporting my view that this is not a new approach as claimed by the authors). However, the authors should have described the rationale for this study more broadly and how they achieved the study objectives. Then they should have defended their choices of specific methods/models with appropriate citations. Section starting at line 79 does not make any sense. Overall, this section lacks the structure required to set the stage for this work.

Typographical errors/language:
1.	Dinamica EGO is consistently misspelled – abstract, lines 168, 201.
2.	Line 97: ‘Specifically’, not ‘Especifically’
3.	Line 97: ‘pessimistic’, not ‘pesimistic’
4.	Line 133: ‘composites’, not ‘compositions’
5.	Line 138: ‘where’, not ‘Where’
6.	Line 190: ‘optimistic’, not ‘optimist’
7.	Line 290: ‘greatest’ not ‘greateest’
8.	Capitalization not required for the land cover class names (lines 332, 335, 336: Primary forest, Areas without vegetation); or they should use those words within quotation marks.
Experimental design: Materials and methods:
1.	Data source: lines 124-130 are not really required, as this is pretty standard for any satellite remote sensing study.
2.	Land use classification (should really be ‘land cover and land use classification’): the authors mentioned that they used Support Vector Machine (SVM) classification while they said they used the R package for random forest, which is an entirely different classification scheme. Unless this is an honest mistake, this would make me very concerned about the technical background of the team. If they insist that they used random forest package for SVM, I would like to see the R codes that they used.
3.	Selection of variables and transitions: then they directly jumped to this section without mentioning anything about the models. I’m assuming this section refers to the data required for the model, but then we need to first understand how the model works and what is required.
4.	Exploratory analysis of data: did they use the threshold of 0.5 (lines 181-183)? Then clearly mention here. Line 166: how do they ‘previously know’?
5.	Simulation of the land use changes: the authors classified 1990, 2005 and 2017 images, but it is not clear from this section which ones were used for simulation.
6.	Validation: this section describes model validation, but does not mention anything about land cover classification validation. In the results section (line 223), accuracy numbers are provided, but they need to describe exactly how they performed the accuracy assessment. Also, for the model validation, I’m not sure if 2005 was used (seems like the case from the figure captions). This section, like many others, requires a complete rewrite.
7.	I’m also not sure how/why they chose 2050. It would make more sense to me to use 1990-2005 transition probabilities to simulate 2017 with three scenarios, include a comparison of observed 2017 and simulated 2017, and then continue with the observed trend for another year, say 2050 (with proper justification). It’s not clear to me why they chose 2005 to compare the observed vs. simulated (Fig. 2). If they have strong reasons, they need to make it clear in the manuscript. But then they mention doing just that in the results section (line 264).
Validity of the findings: Discussion/Conclusion:
1.	The last paragraph ends abruptly. I think they can move parts of the conclusion (lines 367-376) to discussion.
2.	Line 379: this is first time I’m learning that the authors integrated interviews and GIS, no mention of interviews until now.
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: SPATIAL NEAR FUTURE MODELING OF LAND USE AND LAND COVER CHANGES IN THE TEMPERATE FORESTS OF MEXICO
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall a good paper with regard to literature, background, professional article and figures, etc. It needs additional work on English grammar and language editing. Minor details below:

ABSTRACT
Abstract should report the classification validation results-- specifically give the Kappa coefficient.
“For the study, a steady, an optimistic and a pessimistic scenario was proposed” should read “were.”
Primary forest should not be capitalized in the middle of a sentence. Alternatively, all land use types should be capitalized as in the next sentence they authors say “Secondary Forest.”
Use consistant naming of scenarios instead of switching from “steady” to “static,” which are equivalent but could confuse readers.
“primary forest got reduced” should read “was reduced” and clarify what the % refers to—the abstract does not name the study area. All of Mexico?

INTRODUCTION
Line 47-51 check and revise grammar: “Temperate forests of Mexico occupy 17% of the national territory, represented by 32 millions hectares. In this region, the greatest association of pine and oak forests in the world occurs… However, 40 thousand hectares of forests get on average lost annually.”
Line 77: Suggest using a citation relevant to this study like Galford et al. 2015 that used Bayesian WoE for scenarios evaluating policy plans for agriculture and forest in DRC.
Line 80, 83: “celular" should read “cellular”
Line 83: Cite also Soares-Filho et al. 2013 J. Environ. Sftwr. DOI: 10.1016/j.envsoft.2013.01.010.
Line 97: “Especifically” is not a word in English
Line 100 “extemsion” is not a work in English

DATA SOURCE
Line 123 Table 1 seems incomplete
Study area is not well defined. Please provide a description of why this site was chosen.

MODEL VALIDATION
Line 265: Fuzzy similiarity index (FSI) was previously defined so it can just say “FSI” here
Line 266: “DSI” should read “FSI”?

DISCUSSION
Lines 302-305 reads like a summary of the work; rather it should discuss the findings.

Table 5. What does “exchange” rates mean? Rate of change? Including numbers (ha or km2) could be useful in addition to the percentages.
Table 6. Unclear from the table caption and the table itself—what are these numbers? Units?
Table 9 caption should read “projected” instead of “proyected” scenarios.
Experimental design: This primary research examines scenarios of land use change for a study site in Mexico through 2050. The land use change model is parameterized from historical land use change maps. The methods are rigorous and described in detail. Things like the Dinamica-EGO transition matrix are provided, increasing transparency and detail useful to the reader.
Validity of the findings: The Dinamica-EGO platform is utilized for spatial simulation models with Bayesian Weights of Evidence. It is a strong method that is appropriately applied by the authors. The authors use fuzzy similarity index to validate their model, a method that shows good agreement between their simulations and observed data with transparency to the readers.
The conclusions could be more strongly stated instead of reviewing the work that was done.
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: SPATIAL NEAR FUTURE MODELING OF LAND USE AND LAND COVER CHANGES IN THE TEMPERATE FORESTS OF MEXICO
Review round: 2
Reviewer: 1

Output:
Basic reporting: Be consistent with "Weights of Evidence" or "weights of evidence." Both notations are used but pick one and use throughout-- I believe "Weights of Evidence" is standard.

Similarly, "Bayesian" should have a capital B each time it is used.

For references like GloVis, citation should be "USGS 2018" and the reference should list the website address. Do no give website addresses in the body of the paper.

In the Fuzzy Similarity Index figure (4), please make the x-axis units of distance, not pixels. One by one radius of a 30 m pixel would be 15 meters; 3x3 pixels would be 60 meters.
Experimental design: Excellent.
Validity of the findings: Well done.
Additional comments: Nicely improved in this version.


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

Input:
Title: THE CHEMICAL COMPOSITION OF A NEW “MICA SANDWICH” FORAMINIFERAL SPECIES FROM THE EAST COAST OF KOREA: CAPSAMMINA CRASSA SP. NOV.
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper is clear, concise and a pleasure to read. It's a basic report of a newly-found species, with broader comparisons with the type species of the genus.  The description has sufficient detail, and illustrations are excellent, showing the new species in different views.
Experimental design: Fine.  No problems here.
Validity of the findings: I agree that this is likely to be a new species of Capsammina. The Sea of Japan is a semi-isolated body, and endemic species are expected.  This is certainly the case with the Miocene, which is host to many endemic species.

The genus Capsammina was described as being sandwich-like, comprised of a doughnut-like ring of fine agglutinated grains sandwiched between two mica flakes. Kaminski (2014) placed it in the subfamily Psammosphaerinae, because it was described as possessing no obvious aperture.  However, two images in Figure 2 bring this into question.  In the side-view image (fig. 2-3) a hole (or at least a dimple) is visible. In top view (Fig. 2-1), the pavement of agglutinated grains (at 12 o'clock) seems to stem from the position of the hole. Agglutinated grains in the doughnut at this location appear to be mostly coarse, with less fine-grained material.  Is this the aperture? Or is the connection through the more permeable (?thinner) wall at this location?

One thing I do not agree with is the inclusion (albeit speculative) of the species Psammosphaera bowmanni into the genus Capsammina.  Capsammina was described as a "Mica Sandwich", i.e. two large plates cemented together by a ring of fine agglutinated material.  I don't like the inclusion of P. bowmanni for two reasons: First, P. bowmani uses several flakes of mica to construct a polygonal "box".  If we start separating out forms that build their test out of Mica, then we also need to describe a new genus for the species Reophax micaceus.  Secondly, in P. bowmanni and in R. micaceus, the mica flakes are cemented at their edges by a matrix of finer agglutinated particles. This is not the case in Capsammina.

I know that in their original description of the genus, the authors mentioned that P. bowmanni may belong in Capsammina.  No need to repeat this speculation in the current paper.
Additional comments: Good finding!  I agree that this is a new species, and the illustrations are excellent.

However, The genus Capsammina was described as being sandwich-like, comprised of a doughnut-like ring of fine agglutinated grains sandwiched between two mica flakes. Kaminski (2014) placed it in the subfamily Psammosphaerinae, because it was described as possessing no obvious aperture.  However, two images in Figure 2 bring this into question.  In the side-view image (fig. 2-3) a hole (or at least a dimple) is visible. In top view (Fig. 2-1), the pavement of agglutinated grains (at 12 o'clock) seems to stem from the position of the hole. Agglutinated grains in the doughnut at this location appear to be mostly coarse, with less fine-grained material.  Is this the aperture? Or is the connection through the more permeable (?thinner) wall at this location? Would you like to comment on this observation?

One thing I do not agree with is the inclusion (albeit speculative) of the species Psammosphaera bowmanni into the genus Capsammina.  Capsammina was described as a "Mica Sandwich", i.e. two large plates cemented together by a ring of fine agglutinated material. By the way, Capsammina may also cement together shards of angular quartz - I have seen agglutinated doughnuts attached to the flat sides of angular quartz shards in my Arctic material.  I don't like the inclusion of P. bowmanni for two reasons: First, P. bowmani uses several flakes of mica to construct a polygonal "box".  If we start separating out forms that build their test out of Mica, then we also need to describe a new genus for the species Reophax micaceus.  Secondly, in P. bowmanni and in R. micaceus, the mica flakes are cemented at their edges by a matrix of finer agglutinated particles. This is not the case in Capsammina.

I know that in their original description of the genus, the authors mentioned that P. bowmanni may belong in Capsammina.  No need to repeat this speculation in the current paper.


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

Input:
Title: THE CHEMICAL COMPOSITION OF A NEW “MICA SANDWICH” FORAMINIFERAL SPECIES FROM THE EAST COAST OF KOREA: CAPSAMMINA CRASSA SP. NOV.
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Very interesting nauscript, important because of better knowledge of foraminifers and their taxonomic diversity. The species that is described is spectacular because the test structure.
The article is very well written, a new species is widely documented and well-illustrated.
I have only minor comments that could be taken into consideration.
It is worth considering if the abstract requires information about other species of Capsammina (the last two sentences).
In conclusions (the last paragraph) give data about biodiversity in the area of Korea peninsula. In principle, this topic is poorly discussed in the content 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: DOSE-DEPENDENT AND STRAIN-DEPENDENT ANTI-OBESITY EFFECTS OF LACTOBACILLUS SAKEI IN A DIET INDUCED OBESE MURINE MODEL
Review round: 1
Reviewer: 1

Output:
Basic reporting: Review on PeerJ # 29824
« Dose-dependent anti-obesity effects of three different Lactobacillus sakei strains using a diet induced obese murine model”
General comments:
Yosep Ji and co-workers present an article on the anti-obesity effect of 3 strains of Lactobacillus sakei. In the context of growing incidence of metabolic syndrome, obesity, and associated morbidity and mortality, the rational of this research is obvious. In this context, attention should be paid to the microbial part of our diet, and this is mainly provided in fermented foods. It is thus wise to seek modulation of obesity-induced pathology as a result of L. sakei consumption, as it is a member of the Kimchi microbiota. Interestingly, the authors address the dose-dependence and the strain-dependence of anti-obesity effects in of L. sakei. Indeed, two strains, within the same bacterial species, may have completely different properties so that one cannot conclude on the beneficial attributes of a species, based on a single study. The paper is technically sound. The manuscript is clearly written. The reviwer recommends publication of this paper, provided that minor modifications are done.
Minor modifications:
The reviewer recommends changing the title: “Dose-dependent and strain-dependent anti-obesity effects Lactobacillus sakei revealed using a diet-induced obese murine model”
Dose-dependent and strain-dependent, with an hyphen: correct throughout the paper
Line 30&31: rephrase, it is not clear: cause of various…..syndrome
Line 31: pathogenicity: of what?
Line 32: what does remains a poorly defined area?
Line 38: “various … trials”: then more clinical studies should be cited in the paper
Line 66&67: rephrase. Deeper understanding of pathogenesis is needed…..knowledge…is limited
Line 70 and elsewhere : the microbiota
71&72: new clinical diagnostic perspective: define, explain
82: (including development of dedicated in vitro models)
84: distinguish cited preclinical and cited clinical studies
88 to 90: cut the sentence
100 to 109: please evidence the link between these cited reports and your present work.
110 to 112: cut the sentence
117&118: composition of the regimen could be given in a table
128: what was the dose of Orlistat per day? Describe briefly the effect of Orlistat. You could also cite a reference reporting its use in a similar animal study.
134: AST: describe, a marker of ……153: you should add a sentence like “at the end of the treatment, body weight was increased by the HFD. This weight gain was limited by…(Fig.1A)….This figure is not cited…..
RESULTS: use capital letters: 1A, 1B, ….
151-161: it should be mentioned here that only strain CJLS03 has a significant and important effect, I think.
177: noticeable decrease…..results being non-significant, I suggest “a trend in AST reduction”
185: Orlistat treatment resulted in….
208: some selected strains of probiotics have been….208-209: animal studies (…) and clinical studies (…) : separate the citations
209: clinical studies : you should indicate here Kadooka and Woodard, you should also cite the work of Minami et al. : J Nutr Sci. 2015 and Biosci Microbiota Food Health. 2018.
217: the probiotic: which one?
218: in a mice model, as a result of L. curvatus….consumption231: …was found to be lower and dose-independent.
Experimental design: Experimental design is correct, authors could better described the origin of the strains, their use in previous studies, the composition of the diets, LF, HF.
Validity of the findings: Data is robust
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: DOSE-DEPENDENT AND STRAIN-DEPENDENT ANTI-OBESITY EFFECTS OF LACTOBACILLUS SAKEI IN A DIET INDUCED OBESE MURINE MODEL
Review round: 1
Reviewer: 2

Output:
Basic reporting: I have read manuscript titled `Dose dependent anti-obesity effect of three different Lactobacillus sakei strains using a diet induced obese murine model` by Yosep Ji et al.
Topic is very interesting and of high relevance for appropriate use of probiotics.
However, some improvements can be done / considered to be implemented into current version.
Thus, some  relevant aspects seem missed.
My first concern is is relevance of the  model and validity of data supporting   dose dependant effect.
Introduction should  include review of evidence from recent sources in respect to effects of (1) Probiotics – (2) Lactobacillus strains – (3) Lactobacillus sakei on metabolic syndrome cholesterol levels, on type 2 diabetes mellitus, etc., every point in particular;
and refer to most appropriate papers in the field(s), like:
[Hill C, Guarner F, Reid G, Gibson GR, Merenstein DJ, Pot B, et al. Expert consensus document. The International Scientific Association for Probiotics and Prebiotics consensus statement on the scope and appropriate use of the term probiotic. Nat Rev Gastroenterol Hepatol. 2014(8):506–14. https://doi.org/10.1038/nrgastro.2014.66
Reid G, Abrahamsson T, Bailey M, et al. How do probiotics and prebiotics function at distant sites? Benef Microbes. 2017 Jul 20:1-14. DOI 10.3920/BM2016.0222
Bubnov RV, Babenko LP, Lazarenko LM, Mokrozub VV, Demchenko OA, Nechypurenko OV, Spivak MY. Comparative study of probiotic effects of Lactobacillus and Bifidobacteria strains on cholesterol levels, liver morphology and the gut microbiota ino bese mice. EPMA J. 2017 Oct 10;8(4):357-376. doi: 10.1007/s13167-017-0117-3.
Etc.].
This should suggest the hypothesis and the novelty.
Strain / dose specific properties can be considered in – see [Specific properties of probiotic strains: relevance and benefits for the host EPMA J 2018. DOI : 10.1007/s13167-018-0132-z].
Experimental design: Materials section should be written in more detailed manner. Authors can descibe the model, it is not clear in current version, provide the scheme of experiment.
When the probiotics was  given? What was content of HFD?
Why orlistat was used? Does/might it have beneficial effects on metabolic profile??
Was the microbiota analyzed?
What was the duration and stability of effect (dose dependant)?
Some of Matmet data are presented  in the Results section.
Some point might be discussed like:
•	What conclusions can be done based on differences found in brown adipose tissue, liver and femoral muscle?
•	Association of microbiome with obesity and mechanics of beneficial effects and potential implementation to clinical practice.
•	Is L. sakei specific strain for obesity? Is it a part of fermented food?
•	How results can highlight new treatment / prevention approaches in clinical set?
Clear and concise endnotes can be added in the end of the paper.
Validity of the findings: Author studied strain Lactobacillus sakei administered in a high fat diet induced obese murine model using three different doses, 1x1010 CFU, 1x109 CFU and 1x108 CFU.
Authors`s results show that only one strain of L. sakei (CJLS03) induced a dose dependent anti-obesity effect.
Statistical significance is clear, however, the relevance of the model used is of high importance.
Additional comments: I encourage Authors to reconsider article in order to clarify points mentioned above.


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: DOSE-DEPENDENT AND STRAIN-DEPENDENT ANTI-OBESITY EFFECTS OF LACTOBACILLUS SAKEI IN A DIET INDUCED OBESE MURINE MODEL
Review round: 2
Reviewer: 1

Output:
Basic reporting: On my opinion, Authors have implemented extensive improvement into the manuscript and responsed to reviewers` comments. All corrections are relevant.
The manuscript is about to ready for acceptance.
And minor points should be considered for correction before publication, like:

In the Abstract: Conclusion vs `Discussion. This study shows intraspecies …`
I have missed in the text clear description of components of low-fat (LFD) and high-fat (HFD) diets used in this study, only the chemical compounds in Table 2.
Has been the low fat or rather low industrial fat diet considered in research group? Names of products might help understanding and generate dietary recommendations.

Limitation paragraph can be included.

Finallly, once again careful checking for spelling needed.
Experimental design: In the revised version with explanations done the design is relevant to the studied topic.
Methods  described with sufficient detail & information to replicate.
however, I have missed in the text clear description of components of low-fat (LFD) and high-fat (HFD) diets used in this study, only the chemical compounds in Table 2.
Has been the low fat or rather low industrial fat diet considered in research group? Names of products might help understanding and generate dietary recommendations.
Validity of the findings: The findings and conclusions of the study are valid, however limitation paragraph can be included.
Additional comments: On my opinion, Authors have done extensive improvement of the manuscript and responsed to reviewers` comments. All corrections are relevant.
The manuscript is about to ready for acceptance,
minor points can be suggested for correction before 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: MAINTENANCE OF DOMINANT POPULATIONS IN HEAVILY GRAZED GRASSLAND: INFERENCE FROM A STIPA BREVIFLORA SEED GERMINATION EXPERIMENT
Review round: 1
Reviewer: 1

Output:
Basic reporting: This article examine survival strategies associated to seed morphological and physiological characteristics in Stipa brevifolia.

The objectives and hypothesis are important for the area of research
Please, put in chronologic order cites in the manuscript (for example, line 33).
Experimental design: Materials and Methods
Fails to detail the conditions of temperature and light in the tests of germination (lines 105-110).
Please, explain the concept of “germination rate”, it is not clear if you consider germination percentage or velocity of germination (line 116).
I would like to read the previous research that permit me understand the addition of awns to the culture medium for the germinations test (lines 116-126)
In addition, you must justified the election of cabbage seed to verify the factors affecting germination.
Validity of the findings: Results
The presentation is clear. Although are confuse the use of abbreviation for name the treatments.

Discussion
Is correct and the Conclusions are well defined.
Please, to correct references (line 197; 205 De Miguel et al; etc) and number of figures (line 225, is Fig 2 or 3).

References
The references list are incomplete. For example “Liu et al, 2018a” (line 60) did not appears.
Furthermore, some cites are erroneous write, because of first appearance the name instead the surname. For example “Martin & Sala 1990 (line 260) instead: Oesterheld & Sala, 1990.
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: MAINTENANCE OF DOMINANT POPULATIONS IN HEAVILY GRAZED GRASSLAND: INFERENCE FROM A STIPA BREVIFLORA SEED GERMINATION EXPERIMENT
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment.
Experimental design: There are some flaws in experiment design: 1) Seeds of Stipa breviflora generally dispersed in June, and germinated in following season, thus it is important to test new harvest seed germination traits rather than 1 year stored seeds, in particularly when you want to infer their ecological significance; 2) More detailed information about seed germination needed to be added, e.g. germination temperature, light condition; 3) grass species are generally formed as bunch which may contain seedlings, junveils, and adults together, I am not sure if it is reasonable to count seed age based on the basel diameter.
Validity of the findings: This is an interesting subject. However, I am wonder if the current  experiment design and results can address the question proposed in this study. 1) firstly, all the conclusion in this study are based on seed germination traits of stored seeds, however, this is not consistent with true condition in the field. 2) awn have been showed have a large effect on seed germination, what is the potential mechanism? It is so hard to convice me that grazing changed the awn chmeical composition and thus affect seed germination. Further, awn of Stipa species is known to affect seed dispersal and its ancor to soil, how this structure affect seed germination in the field? 3) the author claimed that high germination rate is a potential adaptive mechanism to heavy grazing, how? If seeds try to avoid grazing stress, it seems to they need a longer time to escape the current habitat, and delayed germination and seed dormancy seems to be more adaptive.
Additional comments: No more comments.


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

Input:
Title: EFFECTS OF HANDLING AND SHORT-TERM CAPTIVITY: A MULTI-BEHAVIOUR APPROACH USING RED SEA URCHINS, MESOCENTROTUS FRANCISCANUS
Review round: 1
Reviewer: 1

Output:
Basic reporting: This was a nice clear manuscript, well written and prepared. I enjoyed reading. I apologise to the authors for my delay in getting the review in. This is in no way the fault of the journal
Experimental design: Sound. I do think the story is not as clear as the authors propose, since the animals were both starved and held in captivity. This needs to be clarified
Validity of the findings: Greater context of translocation
Additional comments: General Comments

This paper reports three neat small experiments to test the effects of handling and captivity on short-term organism performance. Usefully, the authors use a tractable invertebrate species to achieve better ecological representation rather than focussing on the cute and fluffy. The authors have missed a context opportunity – translocation of taxa has been suggested as strategy to reduce the effect of climate change on ecosystems (Braidwood et al. 2018), and usefully, the authors have produced data that can inform this debate. The work is competently done and well presented. I do have one small issue that can affect interpretation. The animals held captive were also starved, so in reality, the experiments tested for the effect of captive animals held and handled with no food, rather than captive animals with access to nutritional resources. Some commentary is needed.

Detailed comments
•	Line 39. The link to fitness is tenuous at best. Downplay
•	Line 52 and other places following. Please avoid starting a sentence with “however” – except under the circumstance… ‘However much John ate, he could not stop feeling hungry’
•	Line 60. Rephrase. Evolution has no foresight, hence animals cannot be selected to do stuff
•	Line 61. Adverse environmental conditions will also be sources of stress
•	Lines 90-97. The link between the behaviours measured and what can be inferred from them is not clear. This section needs strengthening
•	Lines 117 – 127. As indicated above, the animals are both starved and in captivity, so you are not just measuring captivity
•	Line 123. Greater discussion of the tags or point to a reference.
•	Line 138 and elsewhere – animals live on or in substrata (singl. Substratum), enzymes act on a substrate.
•	Line 138. Why 180 s?
•	Line 146. This method of estimating aggregation has little support in the literature (see Krebs 1999, for an excellent discussion). With no comparable data for the locality, what is actually being measured here is a spot estimate of density, rather than some estimate of frequency distributions of inter-animal distances. Clarify that is a proxy for aggregation, but please don’t refer to it as an estimate of aggregation for a local population.
•	Line 214 and following: It is illogical and silly to give (pseudo)exact probability values for frequentist tests of hypotheses.  This is because the logic of hypothesis testing only requires that the probability is less than a given alpha.  The silliness is because the P value doesn’t actually tell you anything; in frequentist statistics the P value gives the probability of getting that result if the null hypothesis is correct and the experiment were to be repeated many times.  It does not give the probability of the null hypothesis being correct.  Please change throughout.  Refer to the American Statistical Association statement at http://amstat.tandfonline.com/doi/abs/10.1080/00031305.2016.1154108#.Vt2XIOaE2MN
•	Line 263. To properly measure fitness, you need to measure reproduction (hard, but not impossible in sea urchins) see Don Levitan’s papers (e.g. 2002; 1992)
•	The figures were clear, thank you.

Braidwood, David W., Mark A. Taggart, Melanie Smith, and Roxane Andersen. 2018. "Translocations, conservation, and climate change: use of restoration sites as protorefuges and protorefugia."  Restoration Ecology 26 (1):20-8. doi: doi:10.1111/rec.12642.
Krebs, C.J. 1999. Ecological Methodology. 2nd ed. Menlo Park: Addison-Wesley.
Levitan, D. R. 2002. "Density-dependent selection on gamete traits in three congeneric sea urchins."  Ecology 83 (2):464-79.
Levitan, D.R., M.A. Sewell, and F.S. Chia. 1992. "How distribution and abundance influence fertilization success in the sea urchin Strongylocentrotus franciscanus."  Ecology 73:248-54.