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: MICROBIAL METAGENOME-ASSEMBLED GENOMES OF THE FRAM STRAIT FROM SHORT AND LONG READ SEQUENCING PLATFORMS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Priest et al., present an interesting research paper from the Fram Strait, a body of water that links the Arctic and North Atlantic Oceans. Here, the authors generated short- and long-read metagenomes to reconstitute metagenome-assembled genomes (MAGs) with a view to describe the microbial functionality in this important region. The paper was easy to follow and the conclusions generally satisfactory.
My major concern is that the results and discussion and very much focused on the MAGs generated from a technical perspective. Although the technical quality of this work is very high, there is nothing that reminds us of the value of the Fram Strait by the end of the paper. Since this region is important I expected to see analyses of interesting genes or the like. Alternatively, some literature that describes how unique this region is taxonomically would be valuable also. Only Discussion paragraph 1 (Lines 276-287) mentions the system, but in fairly broad terms.
Experimental design: The experimental design is certainly the strength of the paper. I believe that the techniques applied are well explained and justified.
Since the authors also checked for 5S and 23S rRNA genes, as well as at least 18 tRNAs, please add this information to Table S2.
Validity of the findings: In my opinion the findings are valid and expand what is known about the Fram Strait in terms of microbial genomes. Again, I do wish that the findings touched on the genomic features of these microbes to explain adaptations to this interesting region.
Finally, since this work is among the first to contrast short- and long-read sequencing and assembly to generate MAGs, I would like to see which insights were provided because of the long-read sequencing. In other words, what did the short-reads miss that was captured by long-reads. This would potentially assist readers in opting for long-read sequencing in the future. For example, reconstructing MAGs easier or accessing full-length 16S rRNA genes from MAGs.
Additional comments: The final lines of the abstract (L33-35) are unnecessary in my opinion. This is more of a technical note and doesn't inspire the reader.
Dendrogram is spelt "dendogram" in main text (L204) and supplementary file 2.
Line 137 "*.sam files" should be "sequence alignment maps"
Line 207: "CTD" I'm aware that oceanic researchers know this term, but it may be unclear to a general audience.
Could the nonpareil curves be a supplementary figure?
The table names in the supplementary table don't correspond between the tab name and the table name on the sheet. This makes it confusing to follow.


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: MICROBIAL METAGENOME-ASSEMBLED GENOMES OF THE FRAM STRAIT FROM SHORT AND LONG READ SEQUENCING PLATFORMS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is well written, clear and easy to follow. No obvious spelling or grammatical errors were detected. The article structure is acceptable and the raw data accessible.

Please correct:

Line 114-115: This should be reported in the Results section. Please remove as it is already present in the Results section.
line 209: "phylogenetic diversity". This should rather be "taxonomic diversity" or "taxonomic composition". The same applies to the legend for Figure 4.
Experimental design: The experimental design was based on the collection, sequencing, assembly and reporting of MAGs from the Fram Strait. This included both short and long reads sequencing technologies. This was done to supplement the number of metagenomic samples/data sets currently available for this region which is generally low. Numerous analysis protocols were implemented and a sound methodology followed with regards to analysis and investigation. Albeit relatively sparse with regards to sample numbers, the inclusion of a long read data does add some weight to the manuscript. The methods are adequately described and reproducible.

Please add:

In Figure 1 and Table 1 please clearly identify the origin of the sample, i. e. "Atlantic", "Arctic", "Mixed"
Validity of the findings: As stated above, the number of samples are relatively low but the data is strengthened by the inclusion of the PacBio data. The impact and novelty of the findings are low but as indicated these are not assessed. The authors incorporated various currently accepted applications and tools to produce MAGs which was described as the main objective of the paper. All the data has been provided and is accessible.

Areas of concern:
"Mixed" origin samples -  In line 282 it is stated that "likely of mixed origin" yet in line 230 it is stated "mixed water masses sampled". The authors should clearly identify if this is speculation or if the samples were obtained from a "mixed" source. Did the authors use "Mixed" because these samples did not cluster with the other groupings?

Please address this comment clearly as it has implications for the future use of these datasets by other researcher which is the underlying basis of this publication.

Furthermore,

Line 283: "changes in temperature and salinity". These cannot be inspected as the location, i. e. "Arctic", "Atlantic", "Mixed", is not included in S1.
Line 285: "observable differences". How was this concluded? Visually?
Line 312: "distinct patterns in taxa distribution". Please expand, give examples and indicate how these "distinct patterns" were inferred. Is this only based on the clustering? If yes, we return to the comment above about the "Mixed" samples.
Additional comments: The manuscript has details what the authors set out to do, which is the production of MAGs from the Fram Strait region.

That being said, it is a pity that not more was done with the data. It does seem that energy was lost as so much more is possible.

The methodology and analysis is sound and the availability of the raw and assembled datasets will assist in future research. The addition of long read sequencing data does give more weight to the publication and the pipeline described in the analysis of the long read data may be of importance to other researchers.

As stated above, please clarify and clearly label the sample origins


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: SPACE-FILLING AND BENTHIC COMPETITION ON CORAL REEFS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper is well written. The idea of structural complexity affecting competitive outcomes is very interesting.  The references overall seem a bit old.  I understand that 3D reconstruction of corals/coral reefs is still a new approach, but there has been a lot of research in the last few years, and some of them do look into fractal dimension calculated from coral colonies/reefs.

Here are a couple of specific comments related to background information.

L 99-101. "Coral geometry is generally measured at one scale using Euclidean shapes, but this method fails to capture the complexity of coral geometry."

What are examples of the coral geometry measured at one scale and how do they fail to capture the complexity?  Please briefly explain.

L 111-128.  This paragraph talks about fractal dimension values from different studies.  There are different methods to obtain fractal dimension metrics, and they are not directly comparable (e.g. see Fukunaga, A.; Burns, J.H.R. Metrics of Coral Reef Structural Complexity Extracted from 3D Mesh Models and Digital Elevation Models. Remote Sens. 2020, 12, 2676.)  Please clearly define what type(s) of fractal metric these studies that are cited in this paragraph used, and more importantly which specific fractal metric authors used in the present study.
Experimental design: Authors' research question is very well defined.  More detailed description, especially of the calculation of fractal dimension, should improve the manuscript.

Here are some specific comments.
L 186-191.  Regarding the calculation of surface fractal dimension, was this done in a true 3D space?  Please describe more details.  How did you determine the placement of boxes encasing the structure?  Did you use any software or any custom scripts?

L 191-195.  Is the perimeter fractal dimension still based on a box-counting method?  Please clarify.

L 195-198.  The surface fractal dimension was calculated from 3D models (so it was more like a cube-counting) and the perimeter fractal dimension was from 2D models using boxes, correct? I'm a bit confused.  Also, was the perimeter fractal dimension obtained from the entire coral colony, not just "perimeter"?  So, the 2D models used were basically models captured from the over-head angle?  Or, was it just the "base" of each colony.  i.e. If there is a branching morphology, was is the entire colony captured from the over-head angle or just a small round portion at the base of the colony (the substratum-coral interface)?

L 237. Did you check for multicolinearity?  Or, is this particular statistical method robust to such an issue.  Please clarify for those who are not familiar with the random forest method as there are some many variables in the model.
Validity of the findings: I am not familiar with the particular statistical method used in the study (i.e. random forest), so I cannot comment there.

Here are some specific comments about fractal dimension.

L 276-278. "Finally, if a coral had a surface fractal dimension smaller than two (DS < 2), it would lose features as the resolution increased due to the presence of holes devoid of coral polyps, and the total surface area would be smaller at higher resolutions."

Has this been proven using the specific method of fractal dimension calculation used in this study (if so, please cite the study)?  Estimation of fractal dimension using the slope of regression line sometimes has problems, and I am not fully convinced that this explanation is true.

L 287-289. "Coral perimeters with high (DP = 1.01 ± 0.03), medium (DP = 0.999 ± 0.01), and low (DP = 0.988 ± 0.01) fractal dimension (±SE) did not display any different salient geometric features (Figure 3B)."

I am extremely puzzled by these values less than 1.  Fractal dimension is a measure of irregularity, so fractal dimension less than 1 means that the perimeter was less irregular than a straight line.  I know it happens sometime with some methods of fractal dimension calculation.  Is this (i.e. fractal dimension being less than 1) common for this specific method of fractal dimension calculation used in the present study?  The same goes to the surface fractal dimension being less than 2.

L 305-306. "Coral colonies with low fractal dimensions instead displayed holes, peninsula-like perimeters, and smoother surfaces."

Are these "holes" part of a natural coral morphology?  It is hard to image "holes" in a coral colony.  Where do they come from?  If they are due to photo alignment issues, the models should not be used.
Additional comments: I find this study very interesting and the use of multiscale metric such as fractal dimension in a coral reef study is very exciting.  My main concern with this paper is the lack of clarity in the calculation method of fractal dimension and references to the topological dimension (Dp = 1, Ds = 2).  It is very difficult to accept that a surface and a perimeter are less complex than a horizontal plane and a straight line, and it makes me wonder if this is a some kind of artifact related to the calculation method. The paper also references to previously published values of fractal dimension without specifying what kind of fractal dimension was used in each study.  Fractal dimension values obtained using different methods are not directly comparable.

I also wonder why authors did not try something a bit more simple, such as 3D surface complexity (the ratio of 3D surface area to 2D surface area, similar to the traditional rugosity measure in coral reef ecology).  This would be much simpler to interpret as 3D surface complexity for sure means a horizontal plane, and it seems sufficient to answer authors question.

My suggestion is therefore either to add more detailed information on fractal dimension and provide some proof that Dp < 1 or Ds < 2 are not due to some sort of artifact or to use a metric other than fractal dimension, such as 3D surface complexity.


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: SPACE-FILLING AND BENTHIC COMPETITION ON CORAL REEFS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Language is mostly good, but see my specific comment in the attached pdf.
Experimental design: see attached pdf
Validity of the findings: see attached pdf
Additional comments: My recommendation is between a minor and major revision. The research question is interesting and the approach is suitable. However, I think the paper is overcomplicated in parts. It's an ecological study, but the content is mostly mathematical and it lacks connection between the mathematical descriptions and what they mean in terms of coral biology. In order to make this study more interesting to ecologists / biologists it needs to be simplified a bit and placed in a more ecological context. For example, I'm sure there are studies out there that looked at metabolic rates of at least some of the coral species investigated. Does the assumption that certain morphologies are able to gain more energy per surface area (either through autotrophy or heterotrophy) than others hold true?


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: SPACE-FILLING AND BENTHIC COMPETITION ON CORAL REEFS
Review round: 1
Reviewer: 3

Output:
Basic reporting: See general comments.
Experimental design: See general comments.
Validity of the findings: See general comments.
Additional comments: This study related competitive outcomes amongst corals to structural characteristics (derived from 3D and 2D photo-based modelling) of individual colonies. The work used 50 colonies from 8 different species at several sites around the island of Curacao. The study concluded that the surface fractal dimension was able to explain (positively) a significant amount of variation in competitive success amongst colonies and that the addition of the perimeter distance increased this variance explained (negative relationship to competitive success).  The authors indicated this fits with their hypotheses that greater amounts of tissue available for acquisition of energy should aid in competition while longer perimeters require more resources to defend.

In general I really like this study. It’s uses some novel approaches to quantify 3D structure in corals to evaluate some fundamental ecological processes on reefs and does so by building on a host of previous studies. The study brought together nicely many different threads of knowledge about what mitigates competitive outcomes where corals fight for space.  I think the work will have a wide appeal.  I did have some comments/concerns which I outline below

Major comments
The major conclusion from the study is that surface fractal dimension (Ds) relates positively to successful outcomes in competition.  The explanation for this is that high Ds values reflect an exponential increase in the amount of surface area at increasingly smaller scales.  This is based on an accurate characterisation of what D fundamentally is. Now fractal dimension is a slippery concept and some would argue that having a D value greater than the fundamental dimension may not automatically indicate something is behaving as a fractal as its relatively easy to get a linear descending fit in a box-counting algorithm to any surface on a log-log scale.  But leaving that argument aside, its worth stepping back and asking, if the pattern observed here is driven as suggested, by energy acquisition, would we not expect also to see a relationship just to surface area alone?  Why is that not apparent and what does it meant that it is not?  Related to this, I was also a bit worried about the effect of holes in the models.  I believe these were areas that were trimmed out because they were dead.  And much of the discussion about models with low Ds values centred around them being the ones with holes.  And indeed, thinking about the box counting algorithm works, I can see where the effect of this would be to reduce the number of boxes with mesh in them increasingly as box size gets smaller, thus flattening the curve and giving a lower Ds.  But could the explanation not also be a bit more direct in that corals with lots of dead tissue are fundamentally less healthy and thus are not doing as well in these competitive interactions at their margins?  I would think this would need to be evaluated before a conclusion about Ds could be made so conclusively.

I was surprised not to see more analysis focused on the issue of species effects.  The paper is written as though the effects here essentially supersede any from species alone.  This would be a very interesting conclusion indeed. But I don’t think any of the models looked at interactive effects of the structural variables with species, which would be a necessary analysis to back this up.

I liked the approaches to looking at perimeter length but I think there was some further explanation needed.  For instance, when this concept is introduced very early (ln 81) its not clear how one gets this when most of the discussion is about 3D coral colonies.  What would perimeter mean in that context?  Then when it is explained more fully, the acutal method used to stitch images together is not very clear.  Perhaps this is because I was expecting perimeter to based on a 2D project of the 3D model and was preparing to hear some justification of which projection plane was used.  So I think it would be worth mentioning at the start of the section (ln 160) that different approaches to perimeter were used as well as the merits of each to justify it.

As the study is all about explaining patterns of competition, it becomes important that the method for selecting colonies does not introduce any potential bias.  Not much is said about the actual method for selecting colonies (but should be) other than that they were away from other corals.  I was not clear why this was done, given the objective of looking at competition.

Given the 2D models are distorted, isn’t there an issue measuring polyp diameters from them?  How was this dealt with?

I found figure 6 very interesting.  In theory we should not be seeing any change in D across scale right?...if they are truly fractal. That’s kind of the point of fractals.  So what’s going on here?  Could it be that fractal dimension calcs are inherently constrained by the underlying resolution of models. So this just reflects out inability to maintain very high res models at larger spatial extents?

Minor Comments
Ln 124: Dp is not defined at this point.
Ln 186: what tool was used to get fractal dimension.
Ln 189: need to explain how it was validated a bit more.
Ln 220: 3D perimeter length is somewhat confusing.  Perhaps something like perimeter from model?
Ln 237: “corals” rather than “outputs” right?
Ln 282-285: this sentence is confusing.
Ln 293+: I’m not sure its all the  useful to be talking so specifically about individual colonies by name here.
Ln 319: R2 should be 0.18 according to the figure, not 0.8.
Ln 320: being significant.
Ln 401: surface fractal
Figure 4&5: you need to put the variable name key in the legend.


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

Input:
Title: SPACE-FILLING AND BENTHIC COMPETITION ON CORAL REEFS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The paper is well written, and with the revisions, particularly with the clarification of space-filling dimensions, it is much easier to follow.
Experimental design: Authors' research question is very well defined.  Again, the clarification on the calculation of space-filling dimensions solved all my questions.
Validity of the findings: The results are very interesting, and I can now see how space-filling dimensions can capture more than just the surface area of coral colonies and integrate the measure of roughness/smoothness.  It, however, makes me wonder if the fact that the metric additionally captures the presence of holes confounds the results, especially for losing species.  Coral colonies can have dead or dying areas/patches for any reasons (unrelated to surface area and roughness/smoothness), so having such areas leading to lower values of surface space filling dimension, which then relate to an increased losing outcome, seems a bit circular to me.  To me, the presence of holes itself sort of implies the losing state (more holes = more losing).  I don't think it is serious enough to completely invalidate the results, but the fact that the space-filling dimension used in the study is affected by the presence of holes may need to be addressed in the manuscript.  It leaves me wondering what would have happened if the study was conducted using colonies without any holes (i.e. competitions occurring only at the edges of the colonies).
Additional comments: Thanks again for all the revisions.  The paper is very interesting.


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

Input:
Title: SPACE-FILLING AND BENTHIC COMPETITION ON CORAL REEFS
Review round: 2
Reviewer: 2

Output:
Basic reporting: No specific comments here.
Experimental design: The authors have done a very good job of addressing the concerns of myself and the other reviewers regarding the explanation of methods and analysis.  The switch away from fractal dimension and towards space-filling terminlogy was a good one.

Really the only concern I have left is that regarding my comment that the amount of dead tissue on the colony could be related to the competitive success direclty....rather than via the space filling measure which is also affected by the presence of holes created when these areas of dead tissue were manually removed from the mesh. While I appreciate the addition of a figure to the supplementary material, I didn't find the provided argument very compelling largely because it didn't provid much context for the issue.  That there are a few examples of corals that competed well and had dead tissue doesn't mean there might not be an overall effect here. I think a more convincing argument would perhaps be centered around clarifying that perhpas the number of holes was actually quite small...or their area relative to the colonies? Of course this is harder to make given the importance given to the effect of the holes on the spacd-filling dimension.  So probably the best way to address this would simply be to include a metric related to the amount of dead tissue into the analysis and see if this does indeed have an effect. This could perhpas just be expressed as a percentage of the total colonly surface area, or something like that.
Validity of the findings: Aside from my concern about the amount of dead tissue on the colony being an important measure to consider in the analysis (as outlined above), I had no other concerns about the validity of the finding.
Additional comments: Thank you for your thorough efforts to address all 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: FORECASTING THE COVID-19 TRANSMISSION IN ITALY BASED ON THE MINIMUM SPANNING TREE OF DYNAMIC REGION NETWORK
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article use clear technical terms, however the presentation could largely been improved.

The article includes sufficient background and the relevant prior literature is appropriately referenced, however the introduction is overwhelming, please consider the possibility of move some blocks of text in other, more appropriated sections
The structure of the article is confusing and need to improve clarity.

Figures are of sufficient resolution, relevant to the content and appropriately described but are also largely redundant.
All appropriate raw data have been made available and the submission is 'self-contained'
Experimental design: The research aims and scope are appropriated.
The investigation has been conducted with ethical and technical standards, from publicly available dataset. Methods are sufficiently described, referenced and source code of the analysis is shared to improve the reproducibility.
The research question is relevant, meaningful, of interest and timing. However, is not clear to me how the study contributes to filling knowledge gap.

It is unclear what is the innovative prediction system compared to? And what could be the real benefit of its application.
- On line 187 authors state: “the early-warning signal was issued on March 6, which is about 15 days ahead of the outbreak point. On 9 March 2020, the Italian prime minister Mr. G Conte announced the implementation of placing the country into lockdown”, based on what you said, assuming the decision of implementing the lockdown would take zero time (which is often not the case in democratic republics, such Italy, facing the the first wave of a pandemic emergency), authors method would have give 3 days of earlier warning?
Moreover, lockdown decision could presumably be based not only on new COVID-19 cases but also on socio-demographic and economical consideration.

Here are some other major flaws that may affect the experimental design, and I would appreciate the accounting or the discussion of these points:
- on line 86 “When applied to the region networks constructed based on geographical location and traffic conditions” it is unclear if the traffic conditions you mentioned were used in this analysis. And if yes where do this information came from and where are them shown? Without this information, the system appear based exclusively on proximity.
- Authors claims (in the introduction section?!) that MST-DNM “successfully identify the early-warning signals about two weeks in advance”. How do you define the successful identification? …any identification previous to the actual the peak of the daily cases? How do this takes into account measures of spreading control such as the lockdown, which is subsequent to the early-warning signal? What would have happen to the prediction system in the hypothetical scenario of a fully efficient lockdown or the opposite, no intervention at all? It really is not clear what is the “dependent variable” you are forecasting.
- How can Sardinia be simply excluded from the model? Especially when there could be the possibility of a post-summer virus hotspot? https://www.nytimes.com/2020/09/09/world/europe/coronavirus-sardinia-italy.html. For example couldn’t be considered as connected the regions with boat way connections?
- All these speculations are based on the number of new cases. This completely ignores the number of tested people. The proportion of tested people also are different between regions, since as far as I know the budget and medical resources in Italy are allocated based on regional criteria.
Validity of the findings: Both the method and the field of its application are novel and of interest to a broad audience.
The data on which the conclusions are based are robust and publicly available in a repository from the original source.
There is no controlled experimental intervention and no claims of causation.
The conclusions are appropriately connected to the original question investigated.

However, it is not clear how the goodness of the “successful identification” of the early-warning signals are accessed? And therefor, what conclusion is supported by the results.

In the proposed method strong and tacit assumption were taken for granted (traffic information, region exclusion, screened cases...).

The conclusions are strongly in favour of the proposed method but little evidence of its benefits are described in comparison with other methods.
Additional comments: Too much redundant informations are shown in the figures/tables/supplementary. Only Figure 4 and 5 in my opinion are the best way to describe your 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: FORECASTING THE COVID-19 TRANSMISSION IN ITALY BASED ON THE MINIMUM SPANNING TREE OF DYNAMIC REGION NETWORK
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper represents a noteworthy attempt to define a standard and valid mathematical method (MST-DNM model) useful to point out early signals of actual increases in infectious disease cases, in particular Covid-19. To this end, the Authors applied the MST-DNM model to the Italian daily Covid-19 epidemic open dataset and their results appear to be promising.
Experimental design: It is an explorative observational study performed to evaluate the predictive capability of a mathematical modelling.
Validity of the findings: The findings highlighted by this study are definitely significant. However, such mathematical modelling takes in no account the statistical variability in the health data deriving from various sources.
Additional comments: Limitations and remarks pointed out  should be adequately addressed in the text. Some addional computations are requested.


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: FORECASTING THE COVID-19 TRANSMISSION IN ITALY BASED ON THE MINIMUM SPANNING TREE OF DYNAMIC REGION NETWORK
Review round: 2
Reviewer: 1

Output:
Basic reporting: From previous version:
-Presentation improved: Introduction is now easier to read and Methods are clearer.
-Figure redundancy diminished.
Experimental design: From previous version:
-advantages of the proposed methodology are now clearer, comparison with current methods are now mentioned and extensively described with text beyond the numerical aspects (although no AUC confidence interval and no DeLong or similar test results provided).
-it seemed from your response that you used the presence and type of railways from a trains map as traffic condition (which I agree can be a reliable source) but I cannot spot this information in the paper
-Sardinia concerns were appropriately addressed with the addition of a sensitivity analysis and text rephrasing
-limitation were appropriately added to discussion
Validity of the findings: From previous version:
-traffic information, region exclusion and screened cases concerns were addressed or discussed
Additional comments: The paper improved from the previous version.
All major concerns were partially or fully addressed.

Some confusion remains on ROC curves, beside the SVM comparison. There is no clear description of how these were constructed; is that sensitivity and specificity the rate of correct/false early-alert given by the MST-DNM indicator? Foreach ...day? And how is the correctness defined?


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: FORECASTING THE COVID-19 TRANSMISSION IN ITALY BASED ON THE MINIMUM SPANNING TREE OF DYNAMIC REGION NETWORK
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The Authors have addressed main remarks and issues raised by this reviewer in the Discussion section and improved English.
However, they did not provide any formal test comparing the classification performances of MST-DNM and SVM. The question was: is 0.9318 statistically greater than 0.9076? To that end the Author can apply a test to compare two AUCs, namely:
Z = (AUC1 – AUC2) / SE(AUC1 – AUC2)
where SE(AUC1 – AUC2) is the standard error of the difference.
Z is a standardized normal variable which returns the probability level (P-value) of the observed difference.
SE can be also used to compute 95%CL of the same difference, as previously requested.
Finally, it is suggested removing Figure 7: it is poorly informative and the remaining Figures are more than enough to describe the study.


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: WHAT DO ALEXITHYMIA ITEMS MEASURE? A DISCRIMINANT CONTENT VALIDITY STUDY OF THE TORONTO-ALEXITHYMIA-SCALE–20
Review round: 1
Reviewer: 1

Output:
Basic reporting: - Good theoretical justification of the study.
- The issue of discriminant and content validity of the TAS-20 is clearly explained
- Overall, very good justification of the study.
Experimental design: - In the "Identification of construct" section, the use of the "Other" category was a little confusing. The section appears to mix design and results (including it in the classification but then excluding it). Please make this more clear.
-  Description of the procedure was clear and followed a logical pattern.
- In terms of analyses, I have no expertise in Bayesian hierarchical models, so I don't feel comfortable commenting on the analysis and specifics of the results.
-Another way of analysing the data to test discriminant validity would be to conduct an EFA where all items are entered and the expectation would be that they load on the intended factors (n this case, the respective the scales). Although I'm not in a position to say that the Bayesian option was not appropriate, I wonder if the authors could comment more (apart from the single line provided "In line with previous research ") on the choice of analytical strategy.
Validity of the findings: - I agree with the authors on the idea that examination of the content validity of the TAS-20 has been largely overlooked
- Nothing was done with the observation of reverse scored items, which has been found to be problematic in terms of the scale's validity.
- Nice to see corroborated, from this perspective, the well documented problems with the EOT subscale.
- The conclusion "The present results suggest caution in using the TAS-20 in its entirety as mainly two out of the four key features of the alexithymia construct are represented in the items" is measured and balanced.
- Many of the claims in this paper are well supported with relevant literature.
- That some items overlap with ‘health anxiety’ is a shrewd observation. I'd be careful though in overinterpreting this in that many psychological scales (e.g., those assessing depression) would overlap with medical conditions (e.g., low sugar in diabetes). Clinical judgement, considering context, allows attributing findings to different aspects of the presentation.
- This comment in the conclusions "The TAS-20....is not endorsed to measure alexithymia..." is too strong. No single study can claim this. I partly agree with the findings, but the comment is an overstatement.
- Although the authors acknowledge this point in the limitations section of the submission, using  lay people to be the judge of certain psychological (or any for that matter) disorder/presentation is a bit of a problematic assumption. A crude extension would be a medical condition and the opinion of the person with the ailment. Or asking people with panic disorder if their so called intuitions" are a true reflection of a coming physical episode. Anyway, more on this should have been presented in the intro as a way of justifying this methodology.
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: WHAT DO ALEXITHYMIA ITEMS MEASURE? A DISCRIMINANT CONTENT VALIDITY STUDY OF THE TORONTO-ALEXITHYMIA-SCALE–20
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment, well described, the use of English is professionaly sound.
Experimental design: no comment, solid design. Only limitation in my point of view is the limited number of participants. Please adress this is in the discussion.
Validity of the findings: The authors adress the presence of other measures such as the BVAQ and the TI-AS in one sentence in the discussion. I would like to advise the authors to elaborate on this. The authors correctly state that the TAS-20 has its flaws considering content validity. On the contrary, the BVAQ (with another conceptualisation of alexithymia) looks promoising (see de Vroege et al. 2018; Bagby et al., 2009; Vorst & Bermond, 2001). What is the authors' view on these implications for the construct of alexithymia?

Furthermore, the use of self-report questionnaires like the TAS-20 and BVAQ may be problematic in assessing alexithymia; see Bagby et al., 2006. Please include this in your section about future studies.

Suggested references

Bagby RM, Taylor GJ, Parker JD, Dickens SE. The development of the Toronto
Structured Interview for Alexithymia: item selection, factor structure, reliability and concurrent validity. Psychother Psychosom (2006) 75(1):25–39. doi:10.1159/
000089224

Bagby RM, Quilty LC, Taylor GJ, Grabe HJ, Luminet O, Verissimo R, et al.
Are there subtypes of alexithymia? Pers Individ Dif (2009) 47(5):413–8.
doi:10.1016/j.paid.2009.04.012

Vorst HC, Bermond B. Validity and reliability of the Bermond-Vorst
Alexithymia Questionnaire. Pers Individ Dif (2001) 30:413–34. doi:10.1016/
S0191-8869(00)00033-7

de Vroege, L., Emons, W. H. M., Sijtsma, K., & van der Feltz-Cornelis, C. M. (2018). Psychometric properties of the Bermond-Vorst Alexithymia Questionnaire (BVAQ) in the general population and a clinical population. Frontiers in Psychiatry, 9, [111]. https://doi.org/10.3389/fpsyt.2018.00111
Additional comments: Major point;
table 1 and table 2 are missing in the review file that I downloaded. I cannot advise acceptation of the manuscript before reviewing these two tables. Nevertheless, Vierman and colleagues adressed an interesting topic and explored the content validity of the TAS-20 in an elegant way.


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: WHAT DO ALEXITHYMIA ITEMS MEASURE? A DISCRIMINANT CONTENT VALIDITY STUDY OF THE TORONTO-ALEXITHYMIA-SCALE–20
Review round: 2
Reviewer: 1

Output:
Basic reporting: no other comments, the authors adressed my concerns.
Experimental design: no other comments, the authors adressed my concerns.
Validity of the findings: no other comments, the authors adressed my concerns
Additional comments: I would be happy to advise the editor to accept the manuscript in its current form for publication. I congratualte the authors with an interesting paper and study.

Best regards,
Lars de Vroege


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: VERTICAL ZONATION OF THE SIBERIAN ARCTIC BENTHOS: BATHYMETRIC BOUNDARIES FROM COASTAL SHOALS TO DEEP-SEA CENTRAL ARCTIC
Review round: 1
Reviewer: 1

Output:
Basic reporting: This study reviews the vertical distribution of organisms in the Arctic Ocean based on several previous studies and identifies the biota's boundaries. The methodology itself appears to be sound. The information contained in the paper is valuable and deserves publication.
However, some improvements could be made to the study.

1. Discussion
Most of the discussion merely traces previous research, making it difficult to understand what this study has revealed.
Since you have reviewed the biota based on many previous studies, it would be good to discuss each bathymetric zone's characteristics in more detail based on its constituent species.

Since you have reviewed the biota based on many previous studies, it would be good to discuss each bathymetric zone's characteristics in more detail based on its constituent species.
There is still a lot to discuss, such as why the species are present in that depth zone and whether changes in species composition are common among the three phyla.

You mentioned the Antarctic Ocean, but little about the rest of the world. I think that you should clarify the characteristics of the study area compared to previous studies on the vertical distribution in other parts of the world.

In fact, it would have been better to include some basic information, such as water temperature, which is easily available, to add more depth to the discussion. Still, I leave that to the author since the author declares that he will not do so at the beginning of the discussion.

2. List of species
This is inevitable, given the large number of previous studies reviewed and the wide range of taxa covered, but some errors are apparent.
e.g.
Polychaeta should not be used. Annelida is better.
Travisia is not Opheliidae (now Travisiidae).
We recommend that you check again as there are likely to be many other errors.

Thank you for inviting me to review,
Yours sincerely.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: no comment


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

Input:
Title: VERTICAL ZONATION OF THE SIBERIAN ARCTIC BENTHOS: BATHYMETRIC BOUNDARIES FROM COASTAL SHOALS TO DEEP-SEA CENTRAL ARCTIC
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper is moderately well written. There are typos and missing words throughout, some of which I expect are due to the translational thinking from Russian to English.

Literature is sufficient, but some additional statistical references might be added re ChiSquare
Experimental design: The major problem I have with this paper is the explanation of the statistical analyses.

I have been puzzling over the use of Chi-square as the test distribution and the parabolic shape of the expected values in Figures 2-7. If one looks only at the values for upper and lower limits within a depth range (the blue line) one can see that the values don’t change much, e.g., in Fig. 7, below a depth of 1400 m. Yet, the expected values soon bottom out and then start to go way up, as do the Chi-square values.
l. 145-148 merely states that the expected number of upper and lower limits is summarized. There is no statement in the previous paragraphs about how the expected number of species for each depth interval is derived. One can only guess.
Why do the expected values rise so rapidly with depth? If the class interval expected values are not all equal, then some underlying distribution must have been applied. One thing we know for Chi-square, is that it is notoriously unreliable when values are small, i.e., below 10, and in the case where some cell values are very high and others very low, the cells with low numbers are often combined. In this case it seems that the number of upper and lower limits are routinely pretty low.
Validity of the findings: A few additional comments:

l. 160-165 and elsewhere for the other taxonomic groups…. Is it really a zone of crowding when you have only a small number of limits, e.g., 5 to 10, when the overall polychaete species richness must be quite a bit larger. In other words, if a good survey of the benthos at those depths would produce 50-100 species of polychaetes, then having 5-10 species define a zone of crowding doesn’t make sense since those are only 10% or so of the total.
l. 190-192, as you note, those peaks apply mainly to lower limits. That is not a zone of crowding, but rather a slow depletion of species who have met conditions in which they can no longer exist. One would expect that sort of winnowing with depth as food is steadily being depleted.
Additional comments: In sum, I think the methodological aspects of the calculations need more thorough explaining. I tried finding the Backus paper on the internet, both through Harvard, who said go to Biodiversity Heritage Library, a fabulous site, that alas did not have this volume of the Bull MCZ. So I cannot figure out how the calculations are made, as noted previously.
Because of the low number of records with depth, I am not so sure that Chi-square is the statistic to use. There are some very good books on dealing with categorical data, but unfortunately I am not near my office or I would make some recommendations.
Lastly, I wonder if taking the biocoenosis approach would also be useful as a comparison to the approach used here. I suspect in many ways the limited data might also be a problem for the biocoenotic approach as well.


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: VERTICAL ZONATION OF THE SIBERIAN ARCTIC BENTHOS: BATHYMETRIC BOUNDARIES FROM COASTAL SHOALS TO DEEP-SEA CENTRAL ARCTIC
Review round: 2
Reviewer: 1

Output:
Basic reporting: The manuscript has been revised on the basis of the reviewers' comments and no further comments have been made on my part.
Minor corrections
1. Author should not use "Polychaeta" in the manuscript not only in the excel file.
2. Vedinin et al. (2021) is already open in the journal site as a pre-proof. The author should add it to the reference list.
https://www.sciencedirect.com/science/article/pii/S2352340921003991

Yours sincerely,
Thank you.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: no comment


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

Input:
Title: TAXONOMIC RELEVANCE OF PETIOLE ANATOMICAL AND MICRO-MORPHOLOGICAL CHARACTERISTICS OF CLEMATIS L. (RANUNCULACEAE) TAXA FROM SOUTH KOREA
Review round: 1
Reviewer: 1

Output:
Basic reporting: BASIC REPORTING
The manuscript is poorly written and inaccurate in details. The authors often confuse terms ‘species’ and ‘taxa’; do not operate the Latin singular and plural forms, etc. At the beginning, they stated that their results should help in the taxonomy of the genus Clematis. However, in conclusions, they say that their interpretations (not the results! but exactly interpretations) can be arbitrary and, moreover, they recommend themselves to conduct more investigations. Such a position of the authors is at least a bit confusing. Many sentences in the manuscript are unrelated to the main topic. Many other sentences look like stumps - the authors just mention that somebody published something and that all - no any contextual discussion, nothing. Finally, the manuscript suffers from a lack of good and relative citations. The authors cite many old publications, many of which can be omitted, but do not mention really important and recent publications. For example, they declare that capitate glandular trichomes were never reported for petioles and leaves in the genus Clematis before. And this also confuse. Because, I am sure, many old publications report such trichomes (e.g., Svenson 1941; Keener 1967; Kapoor et al. 1985 and other). Many extensive citations, unclear structure of some sentences, and imperfect English make the manuscript difficult to read.
Experimental design: I believe that the study in general, methods, and outcomes are Ok, and lay in the journal field. The paper represents fascinating results and should be published after improving the manuscript and reconsidering its structure. In particular, it would be good to have a more in-depth discussion on the UPGMA tree. Because some of the close taxa (i.e., varieties of C. fusca) appeared far from each other. I also think that this manuscript can be reevaluated more precisely from the point of scientific soundness after improvement because, at the moment, it is difficult to read and understand.
Validity of the findings: This manuscript does not provide some super high-level investigations, but it represents interesting results that can be useful for further taxonomical explorations. However, it looks like the authors have difficulties with the interpretation of their results. Hence, consequently, conclusions are very unclear and controversial. Figures and tables look Ok. More of my comments and suggestions are provided in the attached file.
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: TAXONOMIC RELEVANCE OF PETIOLE ANATOMICAL AND MICRO-MORPHOLOGICAL CHARACTERISTICS OF CLEMATIS L. (RANUNCULACEAE) TAXA FROM SOUTH KOREA
Review round: 1
Reviewer: 2

Output:
Basic reporting: In my opinion, this paper is fairly good but I would strongly suggest a professional English proofread is needed. There are many grammar mistakes. And some sentence is in organized.

It got enough literature references and has sufficient field background. This article has been written In such a way where we can see the structure of this paper.

I would recommend the petiole morphology picture should be enhanced in order to get clear pictures, do some editing to those pictures using Adobe Photoshop,
Experimental design: This manuscript fulfills the aims and scope of this journal.

The findings answered all the research questions and the research structure is well defined, relevant, and meaningful for plant taxonomy research.

The study using adequate technical and method to fulfill its objective. And the methods were described with sufficient detail and informative.

All methods should be referred to previous used methods, citation is needed in this matter.
Validity of the findings: The results were accepted and well organized, however, I would strongly suggest the authors construct key identification of species to prove that the petiole morphological and anatomical characteristics definitely have taxonomic value for Clematis species studied. The rest is just fine.
Additional comments: Please amend all the mistakes that have been marked in the text. This manuscript has its own scientific value and definitely will be useful for plant systematic and taxonomic study.


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: TAXONOMIC RELEVANCE OF PETIOLE ANATOMICAL AND MICRO-MORPHOLOGICAL CHARACTERISTICS OF CLEMATIS L. (RANUNCULACEAE) TAXA FROM SOUTH KOREA
Review round: 2
Reviewer: 1

Output:
Basic reporting: After the first revision, the manuscript has been significantly improved, so now it can be readable, which is a great success. However, minor spelling corrections and fixing the typos are still required, and I highlighted some of them in the attached file. The worse situation is with a representation of the results and some certain unclear moments in the manuscript. First of all, the manuscript is still overloaded with unnecessary citations with no strict relation to this study. For example, I have no clue why authors decided to cite “Illustrated encyclopedia of fauna & flora of Korea” and “Illustrated woody plants of Korea”, as well as how their outcomes are related to Apiacea, Lauracea, Dilleniaceae, Cunoniacae, and Piperales. Perhaps there is some unobvious logic, but then authors should be so kind to open it to not so sophisticated readers as I am. Moreover, in many places (indicated in the attached file), perhaps due to linguistic limitations, the authors wrote some unclear or controversial phrases that must be rewritten or explained before accepting this manuscript. Finally, the References are poorly formatted and lack DOIs, and must be re-checked. The other few comments I did directly in the text, so please follow them.
Experimental design: The experimental design is still fine. Nothing changed here after the first revision.
Validity of the findings: Findings are valid, just as before.
Additional comments: Dear authors, you did a great job, but there is still some work to do. Just keep in mind, we both want the same - make your publication better. Good luck!


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: TAXONOMIC RELEVANCE OF PETIOLE ANATOMICAL AND MICRO-MORPHOLOGICAL CHARACTERISTICS OF CLEMATIS L. (RANUNCULACEAE) TAXA FROM SOUTH KOREA
Review round: 2
Reviewer: 2

Output:
Basic reporting: I have read the manuscript and found out that this article has fairly good professional English used throughout the manuscript, with sufficient literature references, field background, structured figures, tables, and relevant results. There are only a few changes that need to be done to the manuscript.
Experimental design: Well defined but there are a few details in the referred methodology used in this study that need to be mentioned.
Validity of the findings: The findings are very well discussed and explained, and also clearly stated with figures helps. Conclusions are well stated that linked to the original objective of the study.
Additional comments: Please amend accordingly as stated in the text.

I would suggest the title to “Taxonomic relevance of petiole anatomical and morphological characteristics of Clematis L. (Ranunculaceae) taxa from South Korea’

Simplify the sentence, the sentence is a bit confusing in the abstract.

Add one more reference by V.H. Heywood, R. K. Brummitt A. Culham & O.Seberg (2019); Flowering Plant Families of The World.

Please specify how the identification of species has been done in this study.

Please specify the method used in this study referring to which references for stereo and microscopy technique.

Formalin is hazardous, is there any chance to used Acid acetic: Alcohol. Just curious.


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: TAXONOMIC RELEVANCE OF PETIOLE ANATOMICAL AND MICRO-MORPHOLOGICAL CHARACTERISTICS OF CLEMATIS L. (RANUNCULACEAE) TAXA FROM SOUTH KOREA
Review round: 2
Reviewer: 3

Output:
Basic reporting: the English language is clear and professional.
as the study is concentrated on the anatomical and micromorphological analysis of petiole i think the title should be somehow changed as there is no morphological study. the paper has valuable data on less considered taxa but I think features as the depth of the groove is depended on the parts selected for the study. figures are of high quality and reasonably presented in the text.
Experimental design: the Experimental design is relevant. the samples and the method are ok. applied techniques are perfect. sufficient information is given about the process and methods used.
more populations should be used to extract such results but here one sample for each species is used.
Validity of the findings: I think the populations used for each species should be more than only one sample. if it is available the more replication should be added to these findings. what if the selected samples are not a good representative of the species?
Additional comments: due to the micromorphological and anatomical study, I think the title of the article should be revised. the electron micrographs of the petioles surface are very attractive but I think there should be more description of the observed variation.


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: TAXONOMIC RELEVANCE OF PETIOLE ANATOMICAL AND MICRO-MORPHOLOGICAL CHARACTERISTICS OF CLEMATIS L. (RANUNCULACEAE) TAXA FROM SOUTH KOREA
Review round: 3
Reviewer: 1

Output:
Basic reporting: The authors did a good job! The first version of the manuscript was rather unreadable and very unclear in the representation of the outcomes. There are still some scientifically discursive moments in the manuscript, but its quality was significantly improved, and now it looks really interesting for reading and in-depth analysis. Hence, I believe that it should be published, and if somebody does similar research, he or she will be able to extend such discursive moments in its own paper - to criticize this work or, from the opposite, to support it with new findings. Anyway, now the manuscript looks like a strong finished and reliable scientific report and can be accepted for publication, I guess.
Experimental design: All is Ok and extensively explained in the previous revisions.
Validity of the findings: All is Ok and extensively explained in the previous revisions.
Additional comments: Many thanks to the authors for their work and patience in working on corrections!


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: DEPRESSION AND LOW PHYSICAL ACTIVITY ARE RELATED TO SARCOPENIA IN HEMODIALYSIS: A SINGLE-CENTER STUDY
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript was generally clear.  Relevant background information was provided.

Title: The title may need to be revised, as the data is based on only 34/104 participants.

Abstract: Reflects and reports what the study is about.

Introduction: Relevant background information is provided. The study aim is clearly stated.
Edits
1.	On the Introduction page, at the end of the Introduction paragraph, lines 67-68 need to be reworded as the following: “Therefore, the purpose of this study was to explore……”
Experimental design: The study fits within the aims and scope for the journal. The methods is well described.

Methods:
The Methods are described with sufficient detail and information.
Edits
1.	The authors are not blinded to the reviewers. On the Introduction page (no page number provided), in section title Materials and Methods, lines 73, please state the full name of the Ethics Committee that provided ethical approval.
Validity of the findings: Conclusions are stated and linked to the research question.

Discussion:
The main results of the study are discussed and linked to previous research.
Edits:
1.	Please discuss the strengths and limitations 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: DEPRESSION AND LOW PHYSICAL ACTIVITY ARE RELATED TO SARCOPENIA IN HEMODIALYSIS: A SINGLE-CENTER STUDY
Review round: 1
Reviewer: 2

Output:
Basic reporting: The current manuscript aims to describe the prevalence of sarcopenia in 104 patients on hemodialysis.

However, there are some inconsistencies and I have some questions and specific comments provided below.

In regard to the basic reporting, I would recommend double-checking the manuscript for missing references, as a number of references are missing from both the introduction as well as the discussion (see also specific comments).
Experimental design: The outcomes of the manuscript are beneficial for the existing body of literature around sarcopenia and especially within patients on hemodialysis.
Validity of the findings: No comment
Additional comments: Specific comments:
Introduction:
-	Please be consistent in the use of abbreviations (i.e. physical activity is abbreviated in the abstract as PA, but not in the body of the manuscript).
-	There are multiple references missing in the introduction (i.e. line 53, line 55, line 59, and line 65). Please double-check the manuscript for missing references.
-	Line 49: The second sentence in the introduction is somewhat confusing. The authors describe the prevalence of CRF stages 4 and 5 but then describe they are increased 'by'. Should this be increased to?
-	Line 51: I would recommend rewriting “also, over 0.1 million “ to “Also, over 100.000 …”
Methods:
-	Line 81: It is unclear why the authors have exclusion criteria for blood pressure and heart rate. It would be good to add the reasoning for this in the materials/methods section.
-	Line 102: It is unclear how the SMM and SMI were measured. Was this done by BIA or DXA? And it would be beneficial if manufacturer etc. are specified.
Results:
-	Line 129: The authors describe “The correlation of risk factors with mortality of sarcopenia”. I’m unsure where the mortality of sarcopenia derives from. This manuscript does not seem to measure mortality.
Discussion:
-	Line 151: Please refrain from using the word elderly, but use older adults instead.
-	Line 154: The authors describe that advanced age, long duration of hemodialysis, etc. are associated with sarcopenia and adverse health outcomes. It is unclear what the suggested adverse health outcomes are. These are never described, nor can I find these suggested results.
-	Line 156-165: The authors describe the current body of literature around the prevalence of sarcopenia in hemodialysis patients. This would fit as-is, better in the introduction. In the discussion, it would be valued to relate this information with the outcomes of the presented research.
-	There are multiple references missing in the discussion (i.e. line 168, line 184, line 194, line 196, line 204, and line 207). Please double-check the manuscript for missing references.
-	Line 168: Please add a reference to this statement.
-	Line 177: This sentence is a bit unclear and a rewording would be advised to ensure readability.


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

Input:
Title: DEPRESSION AND LOW PHYSICAL ACTIVITY ARE RELATED TO SARCOPENIA IN HEMODIALYSIS: A SINGLE-CENTER STUDY
Review round: 2
Reviewer: 1

Output:
Basic reporting: The revised manuscript meets the criteria for this section.
Experimental design: The revised manuscript meets the criteria for this section.
Validity of the findings: The revised manuscript meets the criteria for this section.
Additional comments: Thank you for making the suggested revisions, I am satisfied with the revised manuscript.


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

Input:
Title: DEPRESSION AND LOW PHYSICAL ACTIVITY ARE RELATED TO SARCOPENIA IN HEMODIALYSIS: A SINGLE-CENTER STUDY
Review round: 2
Reviewer: 2

Output:
Basic reporting: Basic reporting is good. The manuscript would benefit from an editorial check before publishing, otherwise good.
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Thank you for responding to the comments. The revisions that were made are well explained and sufficient.


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 A THREE-GENE-BASED PROGNOSTIC MODEL IN MULTIPLE MYELOMA USING BIOINFORMATICS ANALYSIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is overall well written. However, I would suggest to do one more proofreading to make sure there are no error such as missing pronouns or determiners, such as in line 62 that should be changed to “which was based”. The structure of the article is professional. Regarding references, I would suggest the authors make references for all the programs, software, and packages, as well as their versions and parameters used. In addition, the introduction should discuss the current state of prognosis models based on RNA-seq or single cell RNA-seq data for MM.
Experimental design: -	Overall, the study should compare their model results to the ones obtained by the prognosis models used today
-	The figures are low quality. Not only in terms of resolution but also in their content. For example: Fig 1a should have a better legend, the labels on Fig 1b are hard to read and no title is provided in the legend and spell out what N and T is, on the network shown on Fig 2 is impossible to see the network structure (it should also show the type of interaction from STRING: direct, predicted, etc). Please make the figure readable and that show what you are trying to show
-	Figure 1c shows pathways related to cancer, but how do the authors explain the KEGG results showing a good amount of non-cancer related results?
-	Line 110-111: Authors should make the distinction between correlation and anticorrelation. Module purple is not highly correlated with cancer, its anticorrelated.
-	Line 115-122: P-values should be adjusted by all comparisons performed. In addition, the hazard ratio/risk ratio and 95% confidence interval should be reported (should also be applied for results associated with fig 7)
-	Line 123-127: Can a prognostic model be constructed based on the expression of the final set of prognostic associated genes and show its performance metrics? What about confounding variables that could explain the difference in the high/low risk groups such as sex, age, tumor characteristics, race/socioeconomics, etc?
-	How can be confident the prognostic associated set can be applied to other patient cohorts? Not all selected genes for in fig 6 showed prognostic value in fig 7. What happens if another cohort is included? Will only a subset of fig 6 work in it? It is important to note that the prognostic markers (and model that should be constructed after it) is based only in one cohort and didn’t fully “worked” in the validation cohort. The authors should show that their final prognostic model and gene set is not biased because of the cohort selected to construct it and can be applied to real world patient cohorts. Perhaps the authors could construct multiple models based on N differentially expressed or WGCNA hub genes, where N is the number of genes used for the prognostic model, and show that it outperforms these other genes and gene sets from other prognostic models from the literature.
Validity of the findings: It is difficult to assess importance and the validity of the findings in this manuscript given the lack of comparisons with current used methods. In addition, the authors should perform further experiments as suggested in the previous section.
Additional comments: No further comments


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

Input:
Title: IDENTIFICATION OF A THREE-GENE-BASED PROGNOSTIC MODEL IN MULTIPLE MYELOMA USING BIOINFORMATICS ANALYSIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper of Pan Y. et al. reports on a bio-informatic analysis of Multiple Myeloma (MM) patients’ gene expression data stored in GEO public repository. The paper is clear and formally conform to PeerJ standard; English language is correct. Figures are explicative and clear. The biological context is clearly illustrated in the Introduction, even though more details might be provided on MM prognostication; in fact, recently several reports deeply explored this field, by comprehensive analyses of patients’ genomic profile, and several prognostic scores have been proposed and/or are employed in the management o f MM patients.
Experimental design: The experimental design of the study is clear and rigorous, the main originality being the use of novel bio-informatic approaches leading to the definition of co-expressed modules of genes in MM patients, as compared to healthy donors. The study is aimed at the definition of novel prognostic markers in MM, a quite modern issue, which has been already explored by several authors, by genomic and bio-informatic approaches. MM plasma cells gene expression profile represents one of the features which have been thoroughly analyzed to this aim.
In the present paper, the use of novel bio-informatic tools highlights the expression of a small sub-set of co-expressed genes, whose up-regulations favorably impact patients’ prognosis.
The methods employed are clearly described and enough informative to be replicated. However, no information on disease stage, or therapeutic treatment or patients’ genomic profile (cytogenetic aberrations) have been provided, nor have been considered in the survival analysis.
Validity of the findings: The overall findings of the study are intriguing, since a list of differentially expressed genes is provided, which has been rigorously defined and might be useful to understand MM clinical behavior. However, the prognostic significance of the deregulated expression of these genes need to be more in details analyzed, for instance by multivariate analysis, considering also all the other already well-defined MM prognostic factors (for instance del(17p) and or International Staging System).
Additional comments: The paper is overall interesting, even though it might be improved with a deeper contextualization of the rationale concerning MM prognostic factors and by a more accurate survival analysis, including factors already known to impact on MM patients’ prognosis.


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 A THREE-GENE-BASED PROGNOSTIC MODEL IN MULTIPLE MYELOMA USING BIOINFORMATICS ANALYSIS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have improved the manuscript accordingly
Experimental design: The authors have improved the manuscript accordingly
Validity of the findings: The authors have improved the manuscript accordingly
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: PHYSIOLOGICAL, NUTRITIONAL, AND MOLECULAR RESPONSES OF BRAZILIAN SUGARCANE CULTIVARS UNDER STRESS BY ALUMINUM
Review round: 1
Reviewer: 1

Output:
Basic reporting: Structure conform
Only 17% of the literature cited with less then 5 years — some update could be relevant
Figures of good quality
Experimental design: Clear definition of research question, relevant and meaningful
Excessive description of analytical methods — determinations with “method X, according to “citation” were enough for common analytical methods
Sufficient information on raw data and experimental design
Validity of the findings: Some results can be better explained and I am not completely satisfied:
Fig 1.2 — legend said that for all, but F is different from the others
— for A, B, C, D and E, “lower letters to compare each cultivar for the four treatments” but what  about roots and leaves? It seems they were compared separately but is not said
—	Please confirm all the letters of Tukey’s test
—	For F legend should be “means” and not “significant means”
Fig.2 — The only comparison is between roots or between leaves. Why do not include interaction?
—	Please confirm all the letters of Tukey’s test
Fig. 5.1 —graphics compare relative variation based on control. It is better clarify legend
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: PHYSIOLOGICAL, NUTRITIONAL, AND MOLECULAR RESPONSES OF BRAZILIAN SUGARCANE CULTIVARS UNDER STRESS BY ALUMINUM
Review round: 1
Reviewer: 2

Output:
Basic reporting: i) The article deals with important aspects for the understanding of differences between varieties of sugarcane under aluminum stress. These differences were observed in physiological, nutritional and gene expression parameters. It is an article that is within the scope of the journal;
ii) The article presents a good introduction, with clear objectives;
iii) As a way to improve the introduction, I suggest using a recent study that involves the identification of genes expressed in sugarcane cultivars subjected to aluminum stress. The study “DOI: 10.3390/ijms21217934 (Rosa-Santos et al., 2020)” may provide some data to improve the text contained in lines 116 - 137.
Experimental design: i) Consistent methodology, with good detailing;
ii) I suggest using information on the choice of genes (Introduction, lines 142-144) in the Methodology section;
iii) Appropriate protocols/methods.  However, I make two suggestions:
A – The information “Leaf +1 is also called the top visible dewlap (TVD) and is the first uppermost fully expanded leaf from the top of the plant that has a visible dewlap or distinct collar. Leaf +2 is the leaf immediately below leaf +1” (lines 214-216), may perhaps be removed;
B – In the qPCR analysis: I have doubts about the type of root sample. Was the entire root system collected or only certain segments of the root? (Line 301). There may be variations in the molecular response in relation to the effect of Al depending on the root zone.
Validity of the findings: i) There is coherence between the information presented in the Introduction, the objectives, and what was discussed based on the results achieved;
ii) Well-designed discussion, requiring few adjustments;
iii) In my opinion, the Conclusion section can be improved. The information discussed at the end of the Discussion section more coherently addresses the objectives of the study. The Conclusion section of the manuscript conveys information more related to perspectives.
In addition, according to the phrase “…imply in new management strategies that allow to allocate the most tolerant variety in places with greater aluminum toxicity” (Conclusion, lines 566-567), and with the previous information presented in the Results and Discussion, was it clear which variety was the most tolerant? The text on "strategies" is confusing.
Additional comments: i) I suggest standardizing the term “varieties” in the manuscript. Suggested change to the term “cultivar”, for example, title in Table 2 and other locations;
ii) Review the references. Few adjustments, for example, line 608, 675, and 788;
iii) I suggest standardizing the information “RT-qPCR or qPCR”. For example, I suggest changing the title of Table 2 to: "Selected genes for qPCR analysis in varieties of sugarcane";
iv) Review the information/descriptions for all figures. Prioritize standardization. For example: in the Figure 1 legend, “Tukey test at 5% significance” appears twice.

In addition, I would like to ask some questions:
A - Why were these three varieties of sugarcane selected in this study? Are there prior assessments of their tolerance and susceptibility to Al toxicity?
B - Based on the following information “There was observed an increase in the leaf expression of three genes related to Al tolerance, indicating that the Al tolerance mechanism in these sugarcane varieties may be related to higher SDH, MDH and SOD gene expression in the leaves” (Results, lines 391-393), I ask the following questions:
B1: We know that the effects of Al on the root are crucial for plant responses. Couldn't the modulated mechanisms in the roots indicate tolerance responses in these genotypes? There are differences between the 3 sugarcane varieties, especially when we analyze the genes expression profile in the roots of RB867515 variety (Figure 5);
B2: We know that SOD enzyme is essential in the antioxidant defense system in plants, but can the increase in its expression definitely represent a mechanism of tolerance to Al?
The expression of other genes (antioxidant enzymes) is essential to explain how different sugarcane genotypes can neutralize oxidative stress. I understand that the term “indicating” was used, but maybe the phrase can be improved and used in the Discussion section (especially when it was discussed about the role of SOD, lines 505-528).
B3: The information “These results point to a differentiated mechanism of resistance among cultivars, where the plant responds as a whole to Al stress” (Discussion, lines 555-556) does it cause confusion?
Mainly because it has already been reported: “There was observed an increase in the leaf expression of three genes related to Al tolerance, indicating that the Al tolerance mechanism in these sugarcane varieties may be related to higher SDH, MDH and SOD gene expression in the leaves” (Results, lines 391-393).
Summary: I suggest a review of the use of this informations.

Final considerations:
Thank you for the opportunity to contribute to the manuscript.
I believe that the manuscript has clear English, but I am not entirely able to give an accurate opinion on grammar.
I consider it a good manuscript and needs some adjustments.
Best Regards,
Reviewer


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: PHYSIOLOGICAL, NUTRITIONAL, AND MOLECULAR RESPONSES OF BRAZILIAN SUGARCANE CULTIVARS UNDER STRESS BY ALUMINUM
Review round: 1
Reviewer: 3

Output:
Basic reporting: The overall quality of English writing should be improved. Some compound sentences, for example, "RB928064 showed a higher transpiration rate and stomatal conductance under control conditions, as well as lower values lower than those of the other varieties in the treatment with Al." should be rewritten into two sentences to deliver a clear message about the results. Please check other compound sentences. The discussions should be concise and consistent with the results. Figures and tables should be appropriately cited in the discussion section when the results were referred to. Many sentences that showed results or discussions from other studies, for example, "Al accumulation is a detoxification mechanism where a chelate is formed between Al and an organic acid", lack appropriate reference citations. Overall writing should be written using a scientific writing style. A good example is a paragraph in line 434-455, where the writing is clear and the discussions were made based on the results obtained from the study. The authors tend to use theories that are remotely relevant to the results of the experiments. So many questions arise in my mind. For example, the sentence in lines 420-425 raised the question of whether the sugarcane used in the experiment was dehydrated and what parameters could be assessed to confirm the water absorption limitation. The figure legends should be carefully written. The legends of figure three did not provide any information about panel C, which showed important results. I feel that the manuscript could be improved with a professional English and scientific wring style.
Experimental design: The research question is not very clear. The authors did not define why they used RB928064 (medium cycle), RB867515 (medium cycle), and RB935744 (late cycle) in the AI treatments. Do these varieties show different Al tolerance levels? The background of these varieties regarding Al tolerance should be provided in the introduction. Many studies usually compared the response of stress-tolerant and stress-sensitive genotypes. The authors may rank these varieties by the Al-tolerant level and focus their discussions on the different responses between plant varieties. I think discussions can be more concise and pertinent.

The methods were clearly described with sufficient detail and information to replicate. The authors may additionally test lipid peroxidation in root to support their discussion about the expression change of SOD gene. ROS generation can be part of the signaling process.

The authors showed that the translocation of Al is one important stress alleviation mechanism. They should test the expression changes of genes that are known to be directly involved in the Al translocation process. In the introduction, the authors mentioned the role of ALS1 and ASL3 genes in such translocation. The expression change of these genes may be tested.
Validity of the findings: The authors should provide complete data. For example, while the stomatal conductance and transpiration rates were compared between control and treated plants, the photosynthetic rates were shown from one condition. The conditions where the photosynthetic rates were obtained were not mentioned. Because the authors mentioned in lines 368-369 that the photosynthetic rates were not affected by the Al treatments, they should provide the results from both conditions. Figure 5 is another example of unclear data presentation. The authors mentioned in lines 380-381 that "The varieties treated with Al of this study presented higher expression of genes related to Al tolerance in comparison with the control (Fig. 5)." In figure 5, the expression of the Polyubiquitin gene was shown as the control. Why did the authors compare the expression of, for example, the SOD gene with the Polyubiquitin gene? The expression of a gene in the sugarcane under treatment conditions should be compared with the expression of the same gene under control conditions. The ambiguous data negatively affects the reliability of the reported results.
Additional comments: All experiments in this study were well performed. However, the interpretation and the presentation of the results are vague. All weak points (the examples above and other similar cases) should be carefully reviewed and corrected throughout the manuscript. The data and the result reports should be carefully checked. The speculations in the discussion should be closely relevant to the results of the study. The authors should focus their discussion on the difference in Al responses between sugarcane varieties rather than the mechanisms by which sugarcane may be used to respond to stress. The expression of genes directly relevant to the Al responses should be investigated. Please add references to all sentences referring to results and knowledge from other studies.


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: PHYSIOLOGICAL, NUTRITIONAL, AND MOLECULAR RESPONSES OF BRAZILIAN SUGARCANE CULTIVARS UNDER STRESS BY ALUMINUM
Review round: 2
Reviewer: 1

Output:
Basic reporting: Good
Experimental design: Correct
Validity of the findings: Everything corrected from first version

My only correction is on fig. 1,2,3 and 4, when legend say
"Fig 1 Root and leaves content..."
Shoud say
Fig 1 Root and leaves mean content...

and the some for the other 3 figures
Additional comments: Good work correcting 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: PHYSIOLOGICAL, NUTRITIONAL, AND MOLECULAR RESPONSES OF BRAZILIAN SUGARCANE CULTIVARS UNDER STRESS BY ALUMINUM
Review round: 2
Reviewer: 2

Output:
Basic reporting: The writing is improved. Figure legends are more clear.
Experimental design: The method is clear. All answers are acceptable, consistent with the scope of work.
Validity of the findings: The concerns are clearly addressed.
Additional comments: The manuscript is greatly improved. All my concerns have been addressed.


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: CHARACTERIZATION OF THE MICROBIOME OF THE INVASIVE ASIAN TOAD IN MADAGASCAR ACROSS THE EXPANSION RANGE AND COMPARISON WITH A NATIVE CO-OCCURRING SPECIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: Throughout the text, there are several times when the correct plural word form or tense is not used. Check sentence structure and also double spaces.
Experimental design: The design is a little unclear and as I detail in the comments below, it needs to be clarified or reanalyzed so that the results are correctly interpreted. The use of dataset A, B, C is a good idea to help the reader understand but it appears pseudoreplicates have been used in the place of true replicates and the analysis may be void or not interpretable.
Validity of the findings: The premise of the article to investigate the invasive range of a relatively newly introduced toad compared to a native frog in the highly diverse and endemic region of Madagascar is a good one. The findings are currently a little unclear due to the analyses, yet the use of the statistical techniques is correct - ANOVA, UNIFRAC, PERMANOVA, NMDS, LEFSE, PICRUST and comparison to Bd database are all appropriate techniques for the data, however, some need to be reanalysed or interpreted so that findings can be interpreted correctly.
Additional comments: Abstract
Suggest adding common name of the toad in the abstract and again in the introduction at Lines 63-64
Introduction
Line 99 – don’t need to capitilise T in toad
Line 105 – forests of Eucalyptus spp.
Line 107 – is this the same as Parc Ivoloina?
Line 108 – I suggest that this sentence - D. melanostictus is known to have a high invasive potential - might be better as the start of a new paragraph. Perhaps there could also be a sentence as to why these toads are considered highly invasive.
Line 122 – include the frog common name
Methods
Line 133 – why 3-4 individuals? Below you state 4 individuals were used – needs to be clarified. And if they were sexed or not this should be mentioned.
Line 132-135 – you state 16 individuals for swabbing, yet in Table S2 there are far more than 16 in total – is this including multiple swabs from each individual? Also in Table S2, for DATASET A there are 9/9 at Site 1 for D. melanostictus. It is not clear to me what this table is referring to. The sample numbers are important when considering the downstream analysis, if sample replicates from the same individual are used in an ANOVA (or PERMANOVA) the result will not accurately represent the data because these are not true replicates, instead they are pseudo replicates with dependency on one another (i.e. from same individual if the case). From reading the methods section and adding the sampling numbers up, it is not clear to me how the analyses were performed or if they were performed appropriately. It is also important to check the homogeneity of variance after a significant p-value results as was found here.
Line 136-138 – what is the meaning/interpretation of this sentence During sampling at these sites, only the most generalist native amphibian species could be found (e.g. P. mascareniensis and Boophis tephraeomystax). ? This does not seem like information relevant to the methods and may do better in the discussion.
Lines 142-45 – it is interesting that site 3 appears to be more urban and yet this is where the invasive toad was not detected in 2014 although in the introduction it states they dominate urban areas. Suggest this could be clarified.
Figure 1 – suggest using shapes and colours in site identification and not just colours to suit people who may be colour blind.
Line 152 – were gut samples pooled from same sex or different sex and was this the same for both species?
Line 152-156 – this is a little confusing, were they stored in RNAlater because I understand this allows. storage at ‘room temp’. The final sentence refers to swabs but was this prior to RNALATER storage. Please clarify and be clear about the timeline of sampling and storage methods as multiple changes in temperature can impact DNA and downstream microbiome analyses.
Line 168 – what two replicates are being referred to here?
Line 173 – 174 – please provide a link as the raw sequences are not found under that Bioproject on NCBI.
Line 177 – low-quality reverse reads aren’t always the case and may still provide better quality when the reads are merged.
Line 194 – suggest you included the summaries on dataset groupings written further down before discussing the rarefaction.
Line 195 – this sentence doesn’t make sense, perhaps there is an extra word included?
Line 237 – is there a need for animal ethics approval here too?

Results
Need to clarify how the ANOVA was computed for diversity as mentioned above because based on the information it seems pseudo replicates were treated as replicates. There is also no mention of PERMANOVA in the methods or how this was conducted or how replication occurred and the measure of homogeneity of variances. There is no mention of the plots used, i.e. NMDS in the methods.
Line 281 – Thia to This
Line 285 – Better to refer to the species or its common name and not the genus since that is what you are referring to in this case.
Fig 3 – not sure why it is presented with multiple taxonomic levels in the LDA/LEFSE plot – better to show one taxonomic level or if this is the lowest level of classification of an OTU, show the identity of the OTU and make that clear so that it can also be compared between both species of amphibians.
Line 312 – were to where
Line 315 – was to were
As with Dataset A, it is unclear to me whether pseudoreplicates are used in the testing of sex differences. As you have no site 2 in one of your sexes, I suggest you test between male and female only using a one way design and remove replication by collapsing pseudoreplicates of repeat samples from an individual toad. Without complete knowledge of how the testing was conducted I can’t comment but based on the number of data points in the NMDS and the methods, these are pseudo replicates and not true replicates.
Line 321-323 – suggest rewording of this sentence, doesn’t make complete sense.
Line 324 – functional and Woodhams analysis need to be described.
For Dataset C as there is no replication, suggest you use the Monte Carlo p-value for PERMANOVA
Line 341 – needs rewording. Suggest: “Higher abundances of the classes Bacteroidia and Clostridia were found in ….”

Discussion
There are some more recent studies in this area that may be relevant to discuss related to Rhinella marina. The lack of observable significant differences (if that is the case once analyses are redone) could be due to lack of replication and should be mentioned in the discussion. It is important to identify when talking about skin or gut microbiome in the discussion. You are not able to say there is a trend towards a different gut microbiome – there is no data that supports this.


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: CHARACTERIZATION OF THE MICROBIOME OF THE INVASIVE ASIAN TOAD IN MADAGASCAR ACROSS THE EXPANSION RANGE AND COMPARISON WITH A NATIVE CO-OCCURRING SPECIES
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: The primers’ (515F and 806R) sequences are different compared to the published ones (such as Caporaso et al. 2011) (the primers here seem reversed), which should be double checked.
Validity of the findings: No comment
Additional comments: No additional comments