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: A NEW LIMESTONE-DWELLING SPECIES OF MICRYLETTA (AMPHIBIA: ANURA: MICROHYLIDAE) FROM NORTHERN VIETNAM
Review round: 1
Reviewer: 2

Output:
Basic reporting: Except for a few syntactical and stylistic errors, the language is easily comprehensible. Some of the figure captions need improvement. I suggest to the authors to scrutinize the MS several times to fix the minor errors.

Literature is adequately reviewed, but some deliberate omissions to important facts have been made, which I have explicitly pointed out below.

The data is shared and the article structure is adequate for a taxonomic description.
Experimental design: The authors take on a difficult taxonomic group and attempt to describe a new species, but there are several important points that are not adequetly covered, especially in regards to taxon sampling. I have highlighted these below in "General Comments to the Author".

The methods used are sufficiently described so that replication is possible.
Validity of the findings: The morphological description for the new species is impressive, and the within Vietnam sampling for a description of a new species is adequate. However, to become a significant contribution for the identification of the species unambiguously, more effort is needed, in the form of better taxon sampling and/or in deeper explanation.
Additional comments: The new species that you are describing is clearly a new species with both genetic and morphological differences. But you need to be sure fo the identity of M. inornata and M. steinegeri on your tree to give credence to the new species that is being described. M. inornata and M. steinegeri are not recognized individually on the tree. Since M. Inornata is the type for the genus, it should be identified unambiguously. For this, you would need a sample, ideally from Sumatra, Indonesia, the type locality for the species.

You say (57-59) “….Pyron & Wiens (2011) confirmed the validity of the genus
58 Micryletta and suggested that Micryletta is a sister taxon to the group composed of Microhyla, Glyphoglossus and Caluella, though with low values of node support….” But Pyron and Wiens also included Chaperina.

I also do not see Chaperina (C. fusca) on the tree (you have Glyphoglossus, Calluella, and Microhyla), which was suggested by some authors as a closely related sister taxon for Micryletta. Could your new species be a/the Chaperina? As the morphological features distinguishing these two are ambiguous and Chaperina has a large distribution from Malaysia, Thailand, Borneo to Philippines. Furthermore, Chaperina sequences from previous studies are available on GenBank.

This issue becomes important given that Micryletta as a genus is still poorly recognized.

Hence, I suggest that you show your genetic results on a tree which includes all the species, especially species which has voucher specimens.

Authors state (119-121) “….and has 120 been used in the most of recent phylogenetic studies on Microhylinae (Matsui et al., 2011; 121 Peloso et al., 2016; Nguyen et al., in press).”  It is not advisable to use “in press” publications to support non-critical points. It is too obvious that it is for a self-citation, and is not a good practice.

(130) “…reducing 1 degree Celcius every cycle, and extension for 1 min at 72°C” consistently use “°C”.

(144) “For outgroups…” you have only one outgroup species. Outgroup is the lineage/s that you root the tree with.

Commas in front of “which” is absent in most instances. Many syntax related mistakes in the manuscript. Please scrutinize closely and correct.

Morphological comparisons with other Micryletta has been done through an analysis of the literature. Using the type specimen is the best way to do this without depending on descriptions of other authors. Since comparisons are based on literature, the clear demarcation and identification of the species on your tree becomes even more important (as I outlined above).

(401-402) “….Micryletta cf. inornata (Boulenger)..” So you have another Micryletta species co-occurign in the same habitat of the new species? This needs further explanation in the discussion. Has these been included in the tree? Or could this be variation of the new species?

(465-466) “…information, we suggest Micryletta nigromaculata sp. nov. be considered as a Data Deficient (DD) species following IUCN’s Red List categories (IUCN, 2016).” Having provided distribution, genetic, morphological and natural history data, one should not claim that species to be data deficient. Then it also looks as if you are undermining your own efforts. There are so many species which do not have even basic distribution data and these are the ones that are generally referred to as data deficient by the IUCN. Hence, try to evaluate the species at least based on Area o f Occupancy and Extent of Occurrence.

Figure 3 Caption “Male holotype of Micryletta nigromaculata sp. nov. (ZMMU A5934) in life”. Awkward phrasing. You could say “Holotype of Micryletta nigromaculata sp. nov. (ZMMU A5934), male, in life”. But some of the pictures suggest that the animal is not photographed “in life”. Please check.

Figure 4 caption - It is awkward to say “male holotype…” you could say “Holotype of M. nigromaculata sp. nov. (ZMMU A5934), male….”


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: RELATIONSHIPS BETWEEN NEUROPSYCHOLOGICAL AND ANTISACCADE MEASURES IN MULTIPLE SCLEROSIS PATIENTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Line 292 “less prone to be affected by confounding cognitive, visual and socio-demographic aspects” needs citations, because I suspect that this may be incorrect, and that AS task performance might be confounded by cognitive, visual, and socio-demographic aspects. Certainly AS task performance is altered by cognitive deficits, as pointed out in line 310 of the present manuscript: slow cognitive responses are expected to cause poor performance in the AS task. Visual factors might affect antisaccade tasks: if a participant cannot see the fixation cross well, it may be more difficult to make fast and accurate saccades to the mirrored location. Socio-demographic aspects may relate to a participant’s ability to clearly understand the (somewhat complex) task instructions involved in looking quickly and precisely to the mirrored direction of a cued location.

Minor comments:
The language is detailed, professional, and generally clear. The phrasing of lines 113-114 and 182-184 should be improved.
Line 38: “i) to investigate if antisaccades performance in patients with multiple sclerosis” is not a complete thought. Investigate if they what?
Line 95: “Some studies that looked” should be “Some studies looked”
Line 114 “poor readers may have less interference in the Stroop test than good readers” needs a citation, and/or further justification.
Line 130 “was also recruited” should be “were also recruited”
Experimental design: I have few concerns about the study design.
Was the test battery administered to the MS group before or after the antisaccade task? This is not clear from the manuscript. The test battery should have been administered after (or on a separate occasion), as the antisaccade task results might be altered by fatigue: the MS group, fatigued by the test battery, would then have more errors or longer latencies on the antisaccade task, relative to the control group (who did not take the test battery and were therefore not fatigued). Differences could no longer be clearly attributed to MS, as they might be due to fatigue.
Those with “clinically visible oculomotor abnormalities (e.g. nystagmus or internuclear ophthalmoplegia)” were excluded. It would be best to provide a full list/table of the abnormalities that were cause for exclusion—and to provide the number of potential subjects that were excluded—as the antisaccade test may potentially be invalid for similar patients in the future. Just as the Stroop test cannot be used in colorblind patients, the antisaccade task cannot be used in patients who have known saccadic abnormalities for reasons unrelated to MS. Because the motivation behind the current study is that the Stroop test is invalid in some cases, the cases where this other test is also likely to be invalid should be made clear.
Line 152: “One or two blocks of 8 practice trials” How was the number of blocks of practice determined? Did the MS group receive more or less practice (on average) than the control group? If the practice was not equivalent between groups, this may have led to some differences between the groups.

Minor comments:
What version of Matlab was used?
What size (dva) were the crosses and the gaze-contingent box? These details should be included in the manuscript. I believe that the figure is not to scale, though this is not made explicit.
Were the crosses and the gaze-contingent box white or yellow? They appear yellow in the figure.
Validity of the findings: The findings appear sound, and conclusions are generally appropriate.
The authors conclude that the present findings show antisaccades to be “selective” for inhibitory control in MS, and it is not clear to me how this has been demonstrated. The present results demonstrate that the antisaccade task outcomes are altered by MS, even in early stages of disease severity. But other aspects of MS may drive these differences, rather than deficits in inhibitory control per se. Further, it is not clear that these measures are selective for MS per se, or if the same differences would be present in other comorbid conditions (excluded from the tested population).
It is unclear why statistical comparisons between the MS and control group for prosaccade latencies and corrective saccade latencies are not presented. Similarly, the AS peak-velocity section does not discuss any comparisons between the MS group and controls, despite the stated aims of the study. Corrective saccades should reach a higher peak velocity than antisaccades, as they need to travel a larger distance (and saccades follow the main sequence). This unsurprising finding was confirmed, but no MS vs control comparison is presented for peak velocity, including in the table of correlations with the Stroop test.
The raw data are provided, can be opened, but are not well described. What do the different “sac_type” values correspond to? Which eccentricity is “trial_ecc” 1 and which eccentricity is “trial_ecc” 2? Is “trial_direction” 1 to the left or the right? I thank you for providing the raw data, however your supplemental files need more descriptive metadata identifiers to be useful to future readers.
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: RELATIONSHIPS BETWEEN NEUROPSYCHOLOGICAL AND ANTISACCADE MEASURES IN MULTIPLE SCLEROSIS PATIENTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: The authors have performed detailed analyses of antisaccade (AS) task performance, a widely studied measure of oculomotor movement, in patients with multiple sclerosis (MS) and age- and gender-matched controls. A key premise of the current study is that the AS task may distinguish MS cases to a comparable degree as the standard Stroop interference test, while being more robust to nonspecific effects of neurocognitive functioning. Key analyses include tests of types of saccade (prosaccade, corrective, and antisaccade) in cases and controls, and correlations of AS latency with neurocognitive performance in cases. Overall, the paper is clearly written, the hypotheses are clearly stated, and adequate experimental detail is provided. Our main concern is the rather limited discussion of the potential implications of this work, namely with respect to the relevance of inhibitory control in the onset and progression of MS, and the potential of these findings to inform clinical practice. Some other comments are detailed below.

# MAIN SUGGESTIONS
- some commentary on the practicality of the AS task as an alternative to the Stroop is warranted (e.g. in terms of adminstritation of the test, required equipment, etc), as especially in terms of clinical utility.
- are "normative" Stroop results available? Couldn't the magnitude of these deficits (compared to healthy controls) be summarized here, as you show for the neuropsychological tests?
- at line 176-178, the authors state that "all neuropsychological tests have normative data for the Portuguese population". This is taken as implying that the these tests have been translated into the Portuguese language and administered to native Portuguese speakers, with results consistent to those observed for native English speakers. This is important to note, but really speaks only to the validity of these tests when translated from English. This doesn't speak to the extent of inter-individual variability in any given population, nor are these results a substitute for measuring neurocognitive performance in controls.
- did you correct for age and gender in your analyses? It is understood that controls were age and gender matched, but this is not equivalent to accounting for possible performance differences among people aged 18-45, etc.
- Table 4: the use of "ns" instead of displaying non-significant p-values (and correlations) is not widely preferred (there is a difference between 0.056 and 0.95), inconsistent with Table 2 (you don't do this here), and frankly a bit lazy. You might also want to spell out this abbreviation under the first table to use these.
- lines 113-115: please provide a citation for limitations of Stroop test with respect to inhibitory control, i.e. difference in performance among "good" and "poor" readers.
- Figure 1B: what are the thinner red lines here? These are not explained and as such only detract from the readability of the figure.

# MINOR ISSUES
- line 148: please spell out the first use of "SDK" (software development kit?)
- the use of commas throughout the manuscript is somewhat erratic
- line 174: "fonetic" should be "phonetic" (Portuguese vs English spellings...)
- lines 68-69: typo "this his task"
- line 183: should be phrased as "can lead to different and somewhat unexpected results"
- line 212: incomplete sentence; should be "Bonferroni correction *was applied* for multiple comparisons"
- line 254: should read "A model similar to *that* reported for latency"
- Table 2: "Trail making Man" should be "Trail making Men" ("Trail making (Men)" is preferred)


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: AN AUTOMATED, HIGH-THROUGHPUT METHOD FOR STANDARDIZING IMAGE COLOR PROFILES TO IMPROVE IMAGE-BASED PLANT PHENOTYPING
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: In the work of Jeffrey C Berry and co-authors the high-throughput method for standardizing image color profiles to improve image-based plant phenotyping is presented.

The authors used the Scanalyzer 3D-HT plant-to-sensor system for obtaining digital images of plants. A ColorChecker Passport Photo with a palette of 24 colors was placed in the area of the frame, which was used for color correction by the method described in Gong et al., 2016 and described in MATERIALS AND METHODS, Standardization Method. For each image, the authors estimated the variance of the observed colors from the reference values and obtained several interesting results:
Dispersion for images obtained at night was higher than for images obtained in the daytime. The authors showed that the differences are due to the use of a fluorescent lamp, in which the luminous flux varies with a lower temperature at night.
The authors calculated a number of quantitative characteristics on the source images and on the images after correction. It was shown that in the calculation of some features (perimeter, height), there is a strong variability in the case of using unstandardized images. This is due to poor-quality detection of the plant contour on the unstandardized image.
The authors constructed a hue histogram for standardized and unstandardized images obtained at day and night. It was shown that the histograms of unstandardized images, made during day and night, have significant statistical differences.
In conclusion, because the color profile of the leaves of the plant varies with the concentration of nitrogen, the authors performed clustering of standardized and unstandardized images obtained at night. It was shown that the separation, depending on the nitrogen concentration, is observed for the group of standardized images.

There are a number of remarks to the paper:
1. The article does not explain why the correction method (Gong et al., 2016) was chosen and no comparison is made with other existing methods. There are works in which it is shown that the transition from the RGB color space to the XYZ space can improve the quality of the correction.
Mackiewicz M., Andersen C. F., Finlayson G. Method for hue plane preserving color correction //JOSA A. – 2016. – Т. 33. – №. 11. – С. 2166-2177.
Quintana J., Garcia R., Neumann L. A novel method for color correction in epiluminescence microscopy //Computerized Medical Imaging and Graphics. – 2011. – Т. 35. – №. 7-8. – С. 646-652.
2. Figures 1B and 1D show that as the dispersion of observed colors from the control values increases, the scatter of the measured morphological characteristics varies in different ways. It would be nice to formulate a clear statistical criterion about which morphological characteristics can be calculated without applying the color correction algorithm, and which ones are not.
3. In Figure 1C, the differences between the standardized and unstandardized images are not visually discernible. The correlation coefficients are practically the same. It is necessary to supplement this figure with linear regression equations (the slope and intercept parameters). It would be interesting to compare these parameters between day and night images. Are they differ significantly?
4. For Figure 3C, it is interesting to build variants of clustering for images obtained in the daytime (standardized and not corrected) to make sure that the results will be the same as we see on 3A.

There are several wishes for the work:
1. It is interesting to measure how to change the accuracy of calculating various morphological features when using ColorChecker with 16 colors instead of 24.
2. To detect the plant contour, a threshold segmentation algorithm is used. It is interesting to measure how to change the accuracy of calculating various morphological features using the segmentation method with the adaptive threshold or other more "smart" methods that were mentioned in the DISCUSSION section.
3. The validation of the measured quantitative characteristics of plants does not occur in any way, except for weighing ~ 120 plants. At the same time, if the hardware system used can produce a 3D model of the plant, then it could be used for additional validation of the color correction model proposed by the authors.


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: AN AUTOMATED, HIGH-THROUGHPUT METHOD FOR STANDARDIZING IMAGE COLOR PROFILES TO IMPROVE IMAGE-BASED PLANT PHENOTYPING
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper is written in clear and concise English with only minor errors in grammar and punctuation (i.e. a few missing periods and the parenthetical annotation of references is inconsistent). All of the supplementary data provided could be opened and accessed easily.

The following two items should be corrected

1.	Importantly, the size of the font is too small for the keys in Fig. 2B, 2C, 2D, 3B, and 3B should be enlarged for clarity of the figure panels. I would recommend correcting this.
2.	Based on the figures and materials and methods, the day length should be 14 hours with 10 hours of night (noted ZT 2100-0700), but is noted as a 9 hr night in the materials and methods. This minor correction should be made.
Experimental design: The experimental design is well planned and carried out using robust and well documented statistical analyses. The experiments described and carried out in the manuscript point out an important constraint in phenotypic analyses and point both to a causation of the color variation and a solution for correction in the standardization method outlined in the manuscript.
Validity of the findings: Moreover, the authors provide not only validation of their image standardization method, but also provide an example of improved resolution of N-treatment effects on plant phenotype by using standardization. Thus, they provide strong evidence that color standardization is necessary in image analyses for htp phenotyping data.
Additional comments: Color correction is not only a problem in controlled environment phenotyping platforms but also in field-based systems with fluctuating light. For example, color correction panels are routinely used for field phenomics for crop plants. A recent report : Chopin et al., 2018 Plant Methods “Land-based crop phenotyping by image analysis: consistent canopy characterization from inconsistent field illumination” also describes these issues. The color standardization documented in the current manuscript would be of benefit and perhaps quite useful for field-based phenomic 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: AN AUTOMATED, HIGH-THROUGHPUT METHOD FOR STANDARDIZING IMAGE COLOR PROFILES TO IMPROVE IMAGE-BASED PLANT PHENOTYPING
Review round: 1
Reviewer: 3

Output:
Basic reporting: In this paper Berry et al. report a color correction method that improves image segmentation for a number of image-based features often extracted for phenotypic analysis in plants.  This tactic for improving segmentation is straight-forward and seems to this reviewer to be a method that nearly all plant phenotypers will want to incorporate into their pipelines to improve object segmentation.

Comment: could figure 2, panel A be zoomed in so that the pic is primarily of the plant itself? This would help with any potential to discern a difference between the bottom two masked panels.

Data: I see that the input image datasets are available. Are the corrected datasets available?  It would be nice to be able to try to reproduce the latter based upon direct implementation of the methods and applying those to the former.
Experimental design: Well done.  I am impressed by the both the biological experimental design as well as the computational experimental design.
Validity of the findings: no comment
Additional comments: Nice manuscript. Very timely and useful.

MINOR ITEM:
Spelling error. Palate is a feature of taste or an anatomical feature of the mouth. Palette is the color selection.


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: AN AUTOMATED, HIGH-THROUGHPUT METHOD FOR STANDARDIZING IMAGE COLOR PROFILES TO IMPROVE IMAGE-BASED PLANT PHENOTYPING
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
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: AN AUTOMATED, HIGH-THROUGHPUT METHOD FOR STANDARDIZING IMAGE COLOR PROFILES TO IMPROVE IMAGE-BASED PLANT PHENOTYPING
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Revisions have rendered this manuscript acceptable for publication.


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

Input:
Title: CO-OCCURRENCE PATTERNS OF LITTER DECOMPOSING COMMUNITIES IN MANGROVES INDICATE A ROBUST COMMUNITY RESISTANT TO DISTURBANCES
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The article entitled: “Co-occurence patterns indicate a robust community resistant disturbances during litter decomposition in mangroves” was well done and showed interesting results. However, some modifications are necessary to improve the quality of the paper.

General view:

- Very important: it is important to show the hypotheses!
- English need to be improve
- The text is fragmented on many parts (highlighted for section on next commentaries). There are paragraphs so big and others so short. This situation compromises the reading of the text. Please, improve the writing.
- There are many errors of typing and spelling (highlighted for section). Please, correct them.

Abstract:

- This section is ok. The description of the ideas and the methodologies was well done. However, the discussion needs to be improved. It is important to add a strong take home message! This part is weak.

Introduction:

- Line 40-46: Text fragmented. It is important to become the text more fluid. It could be interesting add information about primary productivity on mangrove sediments on introduction. The litter consumption is the mainly processes associated with carbon cycle on this biome. But this processes in not unique. Please, make mentions about primary productivity on mangroves.

- Line 47-49: This paragraph is exactly the same on abstract. Please, modify.

Material and Methods:

- All collected leaves showed similar phenological stages? Add this information.

- Line 83: Please, add more information about the similarity and/or differences observed on plant species. It is important for understand the possible differences found on organic matter source for microbial decomposition.

- Line 86: The experiment was conducted on replicate? How many replicates? Please add this information

- Line 93: “DNA quality and quantity was evaluated in Nanodrop 2000.” Is the integrity checked on Agarose gel?

- Line 98: As the interest of the authors was to study litter decomposition, why the authors didn’t use others database as CAZY (carbohydrate active enzyme) to upgrade its analysis?

Results:
- Line 129: Please check and correct this phrase – “the only Archaea phylum with normalized relative abundance above 1% was the Euryarchaeota”.

- Line 132: Mixed groups (Clustering based subsystems and Miscellaneous) is a designation that Subsystem curators used to denote experimental system that are works in progress. They should not be included in a manuscript for publication as there are not verified. Should be removed from the analysis.

- Line 151: Hoiwever shift for However

- Line 157: This phrase is displaced. Both? Which? This paragraph could be add on the beginning of line 153. Both (taxonomic/functional) ….

- Line 164: Change proteobacteria and clroloflexi to Proteobacteria and Chloroflexi

- Line 172: proteobacteria to Proteobacteria

- Line 179: Please, put the word Pseudomonas in italic

Discussion:

- Line 204: There are another publications on this thematic. The authors could add these references together with unpublished data

- Lie 229: This sentence justify the add of information about plant characteristics


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: CO-OCCURRENCE PATTERNS OF LITTER DECOMPOSING COMMUNITIES IN MANGROVES INDICATE A ROBUST COMMUNITY RESISTANT TO DISTURBANCES
Review round: 1
Reviewer: 2

Output:
Basic reporting: I believe that the use of scientific English could be slightly improved. There are a few lines with too colloquial statements. But in general, the article can be easily followed.

Sufficient background is generally provided. The article follows the standard structure and raw data is shared, but a number of notes are needed:

The introduction is generally well written. I'd add a short note about how co-occurrence patterns may be important in the mangrove ecosystem, in addition to the already shown general importance. Then, this should be clearly linked to the conclusions section, which now is somewhat disconnected.

In the results, there are a number of lines were the authors tend to partially discuss their results. For instance: L147-L152. This should be corrected and avoided here and through.

I think the way results are presented and the figures need to be greatly improved.
Experimental design: Sampling strategy is adequate. In the methods section, other than specifying the strategic factors (i.e., different mangrooves), it should be stated how many samples were sequenced. Right now it is unclear, and it is crucial to understand the rest of the analysis.

Studying co-occurrence patterns through network analysis is timely and the research question has interest. However, I have missed on how the results of the article fit into the existant litterature regarding litter decomposition, rather than a more general framework (which is ok, but not enough).
Validity of the findings: Again, I think the conclusion could be better connected to the introduction. I think that some speculation and interpretation could be better phrased to be better identified as speculation.
Additional comments: Introduction
L18: change to "macro- and microorganisms"
L26-27: use capital letters in bacterial taxa
L31: low MSPL and high clustering coefficient. Otherwise, it states that both should be low.
L57: different -> specific
L73: scale -> scales

(Methods)
L97. I'd add here the mean length of retrieved sequences. Otherwise, it could be added in the next section.
L113-114. Odd sentence. Rephrase.
L120. About node properties. I recommend describing these more to better understand their ecological significance.

(Results)
L126. Here and through, bacterial taxa should be in capital letters.
L151. Hoiwever -> However.
L151. Also, add environmental overlap as an option between brackets.
L155. Striking. Why striking? These evaluations should be saved for discussion and supported accordingly. The fact that some taxa within the same phyla are associated could be explained by functional redundancy or environmental overlap, through a phylogenetic conservation of traits. Develop on this within the discussion.
L173-175. Again, discussion.

(Discussion)
L208: 'so much'. Avoid colloquialism here and through.
L214. Rephrase.
L220. Rephrase.
L232. 'lead us to propose'. I believe that the level of co-occurrence is a fact based on the shown results. I'd expand on why is this pattern found.
L253-L256. Discussing ecology of Proteobacteria in 4 lines lacks ecological significance. Again, split at least classes within Proteobacteria.
L275. i.e. plant ... -> remove i.e and state factors used in the study. Also, I believe that 'differences in the environment' is not accurate since there is not a report of environmental variables. Maybe habitat or site could be more appropriate.

(Figures)
FigS1, S3, 3: and 6 I do not think it is required to duplicate a figure in the supplementary documents.
FigS2. I'd replace the scientific notation in the axis.Also, the first boxplot has no legend. In addition, to make the figure clearer I'd shrink dot size. Also, I think it would be of interest to split Proteobacteria into its main classes. Also, to improve clarity and significance of the figure, I'd optionally remove those bacterial groups were Betweenness is 0, specifying so in the legend.
Fig S2 and S4: maybe reorder the x-axis by mean/median to improve clarity.

Fig1: are these barplots per sample? If so, I understand that the number of samples taken was 21?. Since there are few differences per sample, i'd consider to regroup these into factor levels through averaging profiles (i.e., one single barplot for Avicenia, other for Laguncularia...). In the B panel, I recommend to split Proteobacteria into its main classes (i.e., alpha, beta, gamma...).
Fig2. Are these nMDS done solely with the annotated orfs?, I think further clarity should be provided.
Fig 4. Definitely, legend should be improved. I think that you could group many taxa into an 'others' category to improve the visibility of the figure. For example, all those taxa with < 2 nodes, but I'd leave this to the author's criteria.
Fig 5. Same philosophy than Fig 4. Here I see two options. Or group some categories into an 'others' cluster (therefore, reducing the number of colors to 4-8), or simply removing colors if they want to highlight the abundance-betweenness relationship.


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: CO-OCCURRENCE PATTERNS OF LITTER DECOMPOSING COMMUNITIES IN MANGROVES INDICATE A ROBUST COMMUNITY RESISTANT TO DISTURBANCES
Review round: 1
Reviewer: 3

Output:
Basic reporting: - In this manuscript the authors investigated the bacterial community associated with mangrove leaves decomposition in mangrove sediments in Brazil. Although the main issue is very interesting, with the possibility to generate new information regarding the role of microbial communities in the decomposition, the dataset is poorly explored and no novelty is presented.
- My main concern is related to the lack of hypothesis. What is the main hypothesis of this study? The manuscript is merely descriptive and focused only on the results of the network (please see comments below).
- The authors did not find differences between the treatments for both taxonomy and functions, and I have some concerns about these results. First, it’s not clear what is the taxonomic and functional level used for the analysis. Reading the paper it seems they analyzed at phylum/class level. In order to get differences I would suggest to go deeper in the analysis.
- Why the analysis was conducted only after 60 days? In order to assess the community dynamics would be adequate to at least have the point zero analysis, to compare the beginning to the end of the chronosequence. Maybe no difference was found because the community was already established after the 60 days. Also, in order to detect the selection of specific groups in the decomposition of the plant material, a comparison with the community of the mangrove sediment is necessary.
- Considering that the authors are trying to assess the community related to decomposition, specific microbial groups and functions should be the focus of the analysis. With the metagenome data the authors could focus on functions related to decomposition and show what is happening comparing the different treatments.
- The most part of the manuscript is regarding the network, however there are several concerns about how the authors conducted this analysis. Why there is only one network? Considering three different mangroves and three different plants I would expect several networks to compare the community dynamics between the treatments.
- The figures are wrongly numbered and make the reading a little bit confused.
- Small typing errors can be found throughout the manuscript. A careful revision is needed.
- What is the possible effect of the bags used in the experiments? Please discuss this issue.
- Please use different symbols in NMDS figure for a better visualization of the patterns.
Experimental design: The experimental design description is very shallow, with the absence of important information to support the analysis and the results. For example:
- What is the location of these mangrove sites? Please provide geographical location.
- Please provide more details about the sampling: how many bags were used per mangrove site? How many samples of DNA were extracted? How many samples were sequenced?
- How could the bag affect the decomposition?
- How many samples were used for network reconstruction?
- Why the samples were grouped for network reconstruction?
- In which taxonomic and functional level were analyzed the data?
- Were the three different plant material mixed?
- Why only one sampling time (60 days)?
Validity of the findings: Considering all the problems raised in the comments above, the findings are not supported by the experimental design and methodology applied. However, considering the dataset I encourage the authors to re-run the analysis and re-organize the manuscript.
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: CO-OCCURRENCE PATTERNS OF LITTER DECOMPOSING COMMUNITIES IN MANGROVES INDICATE A ROBUST COMMUNITY RESISTANT TO DISTURBANCES
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The authors have addressed adroitly the points raised in the review.


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: CO-OCCURRENCE PATTERNS OF LITTER DECOMPOSING COMMUNITIES IN MANGROVES INDICATE A ROBUST COMMUNITY RESISTANT TO DISTURBANCES
Review round: 2
Reviewer: 2

Output:
Basic reporting: Figure use has greatly improved.
Experimental design: Sampling is now better explained.
Validity of the findings: The authors may be wary of linking cause to consequence in their dissertation. However, the experimental setting is strong and controlled, so findings are still relevant.
Additional comments: The manuscript has improved. However, authors should go carefully through the text once more, maybe with the help of an english speaker (or online tools such as grammarly) to make sure grammar is correct. It is understandable that language style varies, but grammar should be correct since English is the standard for science.


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: A NEW SPECIES OF THE ODOROUS FROG GENUS ODORRANA (AMPHIBIA, ANURA, RANIDAE) FROM SOUTHWESTERN CHINA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The language of the present study is understandable but substandard. The authors are requested to use professional language editing before resubmission.
No further issues.
Experimental design: I do not understand the rationale for some data analyses. Why were not all mitochondrial genes concatenated for phylogenetic analyses? Mitochondrial DNA behaves as one and the same locus and it makes little sense to run phylogenetic trees using 12S and 16S sequences, but leave out ND2 sequences and use these for another analysis (Splittree). I suggest to rerun the phylogenetic trees and Splittree using all genes concatenated.
In addition, I would have expected some considerations about the "barcoding gap" in frogs as the authors used genes, which are *the* barcoding genes in frogs and there is ample literature about this (e.g. Vences 2005, Phil. Transact. B 360: 1462; Vences et al. 2012, DNA Barcoding Amphibians and Reptiles, Springer; Murphy et al. 2013, Mol. Ecol. Res. 13: 161-167).
I have another major issue with the "Morphological comparisons" (starting with line 171). These morphological comparisons have in fact the character of differential diagnoses and are as such good. However, the "Diagnosis" (starting with line 229) is no diagnosis, but a description. A species diagnosis has to compare directly the new species with previously recognized ones, explaining that, for instance, species A differs from species B in this or that character. Of course species sharing character states may be lumped together here, but the diagnosis should lead the reader through the characters differentiating the new taxon from previously recognized ones.
Validity of the findings: The authors demonstrate all in all convincingly that they discovered a new frog species. However, the presentation (and language) are substandard and the paper needs to be rewritten in large parts.
Additional comments: This is a description of a new species of frog of the genus Odorrana -- a speciose and difficult genus. The material seems to be scientifically solid, however, I have some reservations regarding the publication of an individual species description in a journal like PeerJ. There are renowned journals (e.g., Zootaxa, ZooKeys) having their domain in the field of taxonomic descriptions, and I would see this paper rather there than here. In 2017 no less than 167 new frog species have been described (Kwet 2018, Elaphe 70) and for 2018 a similar figure is expected. The discovery of just one species description  more does not qualify per se publication in a more generalist journal like PeerJ. I would have expected for such an outlet a more comprehensive revision of Odorrana, but not the description of only one new species.

Regardless of where the paper will end up, at the moment it suffers from several flaws making its acceptance impossible. Besides the issues highlighted above, there are many little issues. I pick just a few examples:

Line 300: it would be much more informative when the authors explain how far distant the three collection sites of the new species are.
Line 305: Etymology -- why is "kweichowensis" referring to the distribution of the new species in Guizhou? I assume that "Kweichow" is an old spelling/transliteration for "Guizhou". Right? If so, you have to explain this. As is, it is completely unclear.
Sentence starting with line 315 ("In recent years...") -- here is a reference lacking. Who has separated these species from O. schmackeri?
Table 1: "kweichowensis" is consistently misspelled as "keichouensis"


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: A NEW SPECIES OF THE ODOROUS FROG GENUS ODORRANA (AMPHIBIA, ANURA, RANIDAE) FROM SOUTHWESTERN CHINA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The English Language of the present manuscript requires a lot of improvement and checking, the paper must be proofread by an English native-speaking colleague. Introduction and Discussion are very short, I would prefer if the differentiation of Odorrana schmackeri complex would be introduced in more details. Structure follows PeerJ standards. Figures, however, are not acceptable at the current state and require a lot of polishing, especially the map (Fig. 1), phylogenetic trees and networks (Figs. 2 and 3) and PCA analysis results (Fig. 4).
Experimental design: Experimental design corresponds well to the objectives of the present paper. However, methods must be described in more details, for example tadpole identification and staging, osteological examinations etc. - this information is omitted.
Validity of the findings: The paper describes one of the lineages of Odorrana schmackeri species complex as a new species based on mtDNA, nuDNA and morphological data. However some statements (i.e. Guizhou province is a center of diversification of the genus Odorrana because it has 12 species recorded in it) appear to be speculative and unjustified and should be removed.
Additional comments: The manuscript is focused on taxonomic analysis of Odorrana schmackeri species complex based on data from mtDNA, nuDNA and morphology. From the data presented by the Authors, I am convinced the new species described in this manuscript indeed represents a new taxon which warrants taxonomic recognition. I congratulate the Authors on this discovery. It is especially important that the Authors applied an integrative approach and used both mtDNA and nuDNA genetic markers as well as morphological characters to assess diversity in this group of frogs. However, the way of data representation, especially figures, requires a lot of polishing and improvement. Also some issues on taxonomy of Odorrana need to be discussed in more detail prior to acceptance of this manuscript. Main issues to be addressed are listed below:
•	Title. Your paper is titled “Odorrana kweichowensis sp. nov., a new species of the odorous frogs…”. This may be is not the most desirable title, since, according to the tradition in zoological taxonomy, it is not advised to use the new species name “prior” to publication of this name: technically all parts of your paper above the line where taxonomic description starts “Odorrana kweichowensis sp. nov.” are “before” the actual description of the new species. That’s why many journals, like many editors in Zootaxa or Zookeys for example, ask authors not to use the new species name before the line where taxonomic description starts, so all these new species should be cited as “Odorrana sp. 1” or similar way. Some editors even insist that the name should not be mentioned in Abstract or Keywords (which may be is not so useful). There is no strict rule on that, but I believe there is no need to give the new name in the title, I think the title “A new species of the odorous frogs (Odorrana, Amphibia, Anura, Ranidae) from the mountain streams of Guizhou Province of China” would be better for your paper.
•	English. I strongly suggest that the Authors revise the English language of the manuscript with help of a English native speaker colleague or paid services for improvement of scientific writing. Right now it is clear that the manuscript was not even proofread before submission, I found numerous mistakes, typos and inaccuracies. The English language should be improved to ensure that an international audience can clearly understand your text; unfortunately this is not always the case in the present version of the manuscript. I am not a native speaker myself, but I suggest that the Authors pay special attention to consistent use of tenses throughout the manuscript. Some examples where the language could be improved are marked in the attached PDF. There are many so I don’t give details here.
•	Introduction. Please always clearly denote what you mean by “Odorrana schmackeri species complex”. A reader can guess what species it includes only after carefully checking the tree. Please define it in the Introduction and provide a brief overview of its distribution and taxonomy.
•	Introduction. Introduction is largely incomplete. Please discuss in more detail about Odorrana schmackeri complex - it's distribution range, previous dtata on taxonomic differentiation within this group of Odorrana, discuss results of molecular analyses of Li et al. 2015 and other authors. Please also mention why the followig species are considered to be the members of O. schmackeri complex: O. huanggangensis, O. yizhangensis and O. lungshengensis. Please provide also a review describing history of splitting of O. schmackeri complex; please discuss phylogenetic results of Li et al. 2015 in more detail. How the clades they revealed correspond to your clades and described members of the complex? They have much wider sampling than you and show more complicated phylogenetic paper… It is not clear what your new data bring to understanding of O. schmackeri complex differentiation compared to previous works.
•	Materials and methods. Please specify how your sampling of O. schmackeri, O. huanggengensis, O. yizhangensis and O. lungshengensis correspond to the respective type localities of these species? Can we be 100% that your samples really include topotypic populations and represent these nominal taxa?
•	Materials and methods. Why you call this research fully observational when you preserved specimens in formalin and ethanol? Please specify how you euthanized specimens. It is unclear in the present version of the paper.
•	Materials and methods. How you prepared skull preparations? Were they stained with alizarin? How many specimens? Nothing is told on that in Materials and Methods, but you provide a drawing of a skull. Please add the relevant section.
•	Molecular analyses. The statement on lines 87-88 puzzles me. You say “Mitochondrial gene segments could be concatenated into one partition because they were effectively inherited as one locus”. I don't agree with this. You combine non-coding - 12S and 16S and protein-coding ND2 genes, so absolutely you must test at least one partition for rRNA genes and three partitions for each codon for ND2 genes. In case you get same recommended models for both 12SrRNA +16SrRNA and all three partitions of ND2 you can join them in one partition. Also, 16S and 12S rRNA genes have usually many gaps in the alignment due to tertiary structure of rRNA molecules. How these gaps were treated in your analyses? Excluded or included? Please specify. I think you should re-run the Modeltest for more detailed partitioning scheme and redo the whole phylogenetic analyses.
•	Morphological analyses. Please unify some morphological descriptions in the Diagnosis, Comparisons and holotype description. For example finger disks are regarded as “pointed”, “tapering”, “cordiform”, etc. It’s all quite confusing.
•	Morphological analyses. Please provide references which you relied on when choosing morophological characters to examine!! Which method of measurement you followed?
•	Morphological analyses. I am very confused - did you used the direct measurements for the PCA, as stated i this is unacceptable and cannot be taken seriously, since it doesn't exclude the body-size component from the analyzed variation. For proper taxonomic analysis you should: 1) Calculate ratio of each character to SVL. 2) Preform PCA analysis for character ratios or loge-transformed character ratios. This will give you real differences in body shape and proportions excluding the impact of differences in body size. Please redo this analysis.
•	Morphological analyses. Same, when comparing morphometric characters between taxa (e.g. longer head VS shorter head) please compare character ratios, not actual measurements (except SVL). Please indicate what statistical tests you applied for testing the significance of differences you recorded.
•	Molecular results. See Lines 167-170. Actually, 2.6-2.8% is not a high degree of divergence in frogs for 16S rRNA gene. Examples you show from other species of Odorrana are not always reliable since there may be mistake in identification of samles or incomplete taxonomy (such as the case of O. tiannanensis and O. bacboensis, most likely). Please refer to papers reviewing degree of variation of 16S rRNA gene in amphibians (see papers by Vences et al. 2006, Vieites et al., 2009 etc) and discuss how your values correspond to species-level divergence in frogs.
•	Molecular results. Your strongest molecular argument is the concordance between nuDNA and mtDNA suggesting divergence of the linage you want to describe as a new species. This concordant phylogenetic signal is very important. However you do not stress or discuss this in your work. Please reconsider.
•	Molecular results. You don't give actual node support values in the text of the MS, nor in Figure 2. Please add PP/BS values on each node for Figure 2.
•	Morpological results. Lines 183-210. Most part of this section must be moved to Comparisons section in the new species description. Please expand and rewrite Comparisons section. Please first focus on differences from other Odorrana taxa and then describe in detail differences from O. schmackeri and all other "related" taxa of the same species group.
•	Morpological results. The measurement accuracy you show in the present manuscript (with 2 decimals after dot) cannot be achieved in amphibian morphometrics. Please round ALL your measurements in the text and tables to one decimal after dot.
•	Species description. Please spell new species name fully without abbreviations everywhere throughout the manuscript, including figures and tables.
•	Species description. How was the species identity of tadpoles evaluated? DNA? Observation of development? Please specify, this should e explained in materials and methods. You staged tadpoles based on Gosner’s tables, but you decided not to cite his work. Please add Gosner’s publication to reference list.
•	Species description. Diagnosis has to be reorganized. In Diagnosis first please give characters based on which the new species is attributed to the genus Odorrana: 1) ..., 2) ..., 3) .... etc. Then please list diagnstic characters for species compared with its congeners.
•	Species description. When writing comparisons of morphometric characters between species or between sexes, please always provide RANGES of characters, not just some values. What are these values? Mean? What is the sample size? Better indicate it anywhere you compare two samples.
•	Species description. Data on natural history of the new species are really scarce. Any idea about diet? Sympatric amphibian species? When and where were animals observed? Etc. Please expand.
•	Discussion. Odorrana schmackeri is also reported for northern Thailand and even Vietnam (see Orlov et al. 2002 and Chan-ard et al. 2011). It has a big range (also please see Li et al. 2015). Please show the range of Odorrana schmackeri on the map in Figure 1. Please demonstrate on the map, how your taxonomic revision devides the range of the species - which populations will remain in O. schmackeri s. stricto, and which become your new species. Otherwise it is very difficult to understand for a reader. This is may be the crucial and most important problem of your paper.
•	Discussion. The statement on the lines 320-321 that “the number of Odorrana species in Guizhou Province has increased from 8 to 12 (Fei et al., 2012), accounting for about 20.69% of total number of species in the genus. And because of that, Guizhou Province is considered to be the differentiation center of the genus Odorrana” appears to be completely unjustified. If you have 12 species instead of 8 in Guizhou province, you can not judge on evolutionary history of the whole genus and claim this is a diversification center! You need to do phylogeny and biogeography analysis for that. Please remove this.
•	Discussion. I think the information you provided is not enough to judge that the new species is Vulnerable. It's rather Data Deficient since more surveys needed. If so, please give reference to IUCN criteria you used for conservation status estimation.
•	Table 1. Please reorganize lines in table, may be better to sort according to species names? Also in this table you use a completely different spelling of the new species as “keichouensis”. Please correct that!
•	Table 2. All measurements should be given to first decimal.
•	Table 3. All measurements should be given to first decimal.
•	Figure 1. This drawing must be reorganized completely: 1) Please provide a map showing elevation (since Odorrana are found in montane areas this is important). 2) Please show the known range of all members of Odorrana schamckeri species complex, inclduing O. schmackeri s. stricto and the know records from Thailand etc. 4) Please provide color figures for localities which would correspond to colors used in Figures 2 and 3. Otherwise it is very difficult to recognize which locality is which species. 5) Please provide legend to locality names and species names to this figure.
•	Figure 2. This figure is difficult to read and needs to be polished. I suggest it's better to separate it into 2 figures. 1) For the 12S-16S tree please make font size bigger. 2) Please use colors which would help to distinguish species of Odorrana schmackeri complex. 3) Please add 12S 16S genetic data for O. yizhangensis and O. lungshengensis which are missing from the 12S 16S tree. 4) Please provide actual node support values for BI/ML analyses, it is much more useful than these circles indicating maximal support everywhere. 5) Please mark the monophyletic O. schmackeri complex and it's members. For ND2 network 1) Better make it a separate figure; 2) Use same colors as in the 12S16S tree and Figure 1.
•	Figure 3. This figure also needs editing. Please use same colors as used for marking clades in Figures 1 and 2. If possible please could you choose more bright colors (green, red, yellow, blue), for color-blind people might be difficult to distinguish the colors you used. For me it's difficult to distinguish between colors of yizhangensis and lungshengensis, for example.
•	Figure 4. This figure must be redone completely. 1) recalculate plots for charcater ratios to SVL, not actual measurement values, to avoid the effect of differences in body size. 2) Please mark that A if for males, B is for females (or which one is which?). 3) You cannot draw borders of polygons like that! You should show minimal CONVEX polygon for each species, you cannot draw borders of these figures as you like. When you plot convex polygons and see how they overlap this shows the degree of differences between samples you compare. Please redo!
•	Figure 8. You need to add signatures for the skeletal features you mention in the respective part of the manuscript and a legend to this figure.
•	Figure 9. There is no “formula” shown in this figure.


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: A NEW SPECIES OF THE ODOROUS FROG GENUS ODORRANA (AMPHIBIA, ANURA, RANIDAE) FROM SOUTHWESTERN CHINA
Review round: 2
Reviewer: 1

Output:
Basic reporting: The current version of the manuscript is greatly improved, the English is also much more comprehensible. I believe the present version of the manuscript can be accepted for publication.
Experimental design: All experiments are described correctly with sufficient details.
Validity of the findings: Presented data are important for taxonomy of Odorrana, the authors report on a new species of the genus.
Additional comments: I thank the authors for their hard work on the manuscript and suggest that the present version can be accepted for publication.


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

Input:
Title: ASSOCIATION OF CYBA GENE (-930 A/G AND 242 C/T) POLYMORPHISMS WITH OXIDATIVE STRESS IN BREAST CANCER: A CASE-CONTROL STUDY
Review round: 1
Reviewer: 1

Output:
Basic reporting: poorly written manuscript
Experimental design: good experiment design and original research
Validity of the findings: data meet the criterion
Additional comments: Association of CYBA (-930 A/G and 242 C/T) gene polymorphisms with Oxidative stress in Breast Cancer: a case-control study
Mohini A Tupurani, Chiranjeevi Padala, Kaushik Puranam, Rajesh Galimudi, Keerthi Kupsal, Nivas Shyamala, Srilatha Gantala, Ramanjaneyulu Kummari, Sanjeeva Chinta, Surekha R Hanumanth
In this paper authors introduced with relationship between common functional polymorphisms of the p22phox gene (-930A > G and +242C > T) and breast cancer as a result of oxidative stress in Indian population. As authors reported here, this polymorphism is highly expressed in breast cancer patients. Furthermore, authors demonstrated that this polymorphism would increase oxidative stress by measuring MDA level in blood samples. They also tried to correlate other factors such as smoking and alcoholism with polymorphism and breast cancer. Author’s case-control study in this paper proves their hypothesis but errors in paper reduced the enthusiasm.
Major points:
1.	Authors could not introduce CYBA (930 A/G and 242 C/T) polymorphism in introduction section. They must add existing research information on this polymorphism.
2.	Authors used telegraphic English and sometime sentence looks incomplete, for example Line 50. Results and discussion sections were not scholarly written. They look like a case report not a journal article.
3.	Authors used MDA quantification to determine oxidative stress. MDA is not sole product of lipid peroxidation, and on the other hand, thiobarbituric acid (TBA) in thiobarbituric acid reactive substance (TBARS) assay dose not determine only MDA. MDA are a measure of oxidative damage on lipids, not of "oxidative stress" per se. Oxidative stress is actually not truly measurable with only one marker: it is a state when oxidant attacks exceed antioxidant defenses, so you need different markers to get the whole picture if you insist on OS.
4.	Major problem I am facing in this manuscript is figures and their legends. Legends are incomplete and does not have information about figures. PDF file I downloaded shows all figures were stretched and quality of some figure was too poor to read.
Correcting these major errors will make the author’s paper look more professional, and certainly should have to be corrected before being accepted for publication.


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

Input:
Title: ASSOCIATION OF CYBA GENE (-930 A/G AND 242 C/T) POLYMORPHISMS WITH OXIDATIVE STRESS IN BREAST CANCER: A CASE-CONTROL STUDY
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment.
Experimental design: Materials and methods description.

There is some missing information, such as:

1-) The period of time in which the study was conducted;
2-) The inclusion and exclusion criteria for entry or not in the study;
3-) The statement informing that this study follows the ethical principles according to Helsinki declaration;
4-) Authors should give more details about the blood collection, such as the patient's position during collection if the patient needs to be in fasting condition, time or period of the day when the blood was collected and what was the vein in which the blood was collected.
5-) Authors also should better describe the MDA assessment in the blood samples of the patients, such as: if there was some previous preparation of the samples before evaluation, including the reagents and the concentrations used in each stage of the analysis. If it was used some specific kit, please, specify the trademark and the local of manufacturing.
6-) Please, include the student´s t-test in the description of statistical analysis, that is missing.
Validity of the findings: No comment.
Additional comments: The study of Tupurani et al. aims to investigate the association between the CYBA gene polymorphisms with oxidative stress in breast cancer initiation and development. The study was well designed, the statistical analysis was properly conducted and the data support the conclusions. However, some minor changes need to be made.

Abstract

The authors can shorter the background section in the abstract and insert the aim of the study, as stated at the end of the introduction.

The authors should briefly describe for what the Insilco analysis was employed in the abstract instead of “Insilco analysis was performed using appropriate tools.”

Introduction

The sentence that defines oxidative stress is lacking reference(s) – Lines 42-45.

Authors are encouraged to point out and briefly discuss the potential limitations of the study. As an example, the last sentence in the conclusions (lines 226-229) authors cited some limitations but they should be in the discussion.


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

Input:
Title: ASSOCIATION OF CYBA GENE (-930 A/G AND 242 C/T) POLYMORPHISMS WITH OXIDATIVE STRESS IN BREAST CANCER: A CASE-CONTROL STUDY
Review round: 1
Reviewer: 3

Output:
Basic reporting: In the current manuscript, the authors conducted a study on 300 breast cancer patients with a comparison to 300 healthy control volunteers to evaluate the association of SNPs: -930 A/G and 242 C/T in the CYBA gene to increased markers of oxidative stress.
In the results section, the authors begin with making a significant claim of the association of non-vegetarian diet, smoking and alcohol consumption with increased risk of breast cancer. However, there have been several such studies  with a larger sample size that have reported no risk associated with non-vegetarian diets and smoking with breast cancer. The association of smoking with breast cancer risk is an issue of debate. It appears that the current study is underpowered and has a small sample size to make such claims. Further, this result is not within the scope of the proposed hypothesis.
Experimental design: Below are listed some of the competing research that refute the claim drawing associations of non-vegetarian diet, smoking and alcohol consumption with increased risk of breast cancer.
1. Lifelong vegetarianism and breast cancer risk: a large multicentre case control study in India
Gathani et al, BMC Womens Health. https://www.ncbi.nlm.nih.gov/pmc/articles/PMC5241933/
2.Active smoking and breast cancer risk: original cohort data and meta-analysis. Gaudet MM, Gapstur SM, Sun J, Diver WR, Hannan LM, Thun MJ. J Natl Cancer Inst. 105(8):515-25, 2013 and Lawlor DA, Ebrahim S, Davey Smith G.
3.Smoking before the birth of a first child is not associated with increased risk of breast cancer: findings from the British Women's Heart and Health Cohort Study and a meta-analysis. Br J Cancer. 91(3):512-8, 2004
4. Moderate alcohol intake and cancer incidence in women. J Natl Cancer Inst. 2009 Mar 4;101(5):296-305. doi: 10.1093/jnci/djn514. Epub 2009 Feb 24.
It is recommend that the authors prepare the manuscript to address the counter arguments present in the literature.

With respect to the C242T polymorphism, a previous study has reported that this variation leads to reduced NAD(P)H oxidase activity in human blood vessels and therefore a decreased production of ROS and vascular oxidative stress. (Xu Q, Yuan F, Wu J. "Polymorphisms of C242T and A640G in CYBA Gene and the risk of coronary artery disease: A meta-analysis." PLoS One. 2014; 9(1): e84251). This opposes the hypothesis of association with increased ROS production as reported in the current manuscript.
Validity of the findings: The insilico analysis reveals interesting results with mRNA structure prediction, transcription factor binding and 3D protein structure prediction which will need further validation by in vitro experimentation.
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: ASSOCIATION OF CYBA GENE (-930 A/G AND 242 C/T) POLYMORPHISMS WITH OXIDATIVE STRESS IN BREAST CANCER: A CASE-CONTROL STUDY
Review round: 2
Reviewer: 1

Output:
Basic reporting: English text needs revision by a native or by a specialized company in this kind of service.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: The manuscript was significantly improved after the first review. However, minor changes should be made before it can be accepted.

English text needs revision by a native or by a specialized company in this kind of service;

The sentence in the discussion “In contrast several reports have been inconsistent, wherein no significant association was observed with respect to smoking and alcohol consumption in breast cancer patients (Byrne, Rockett & Holmes, 2002; Allen et al., 2009; Gathani et al., 2017).” should be placed along with the next paragraph, where this matter is discussed.


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

Input:
Title: ASSOCIATION OF CYBA GENE (-930 A/G AND 242 C/T) POLYMORPHISMS WITH OXIDATIVE STRESS IN BREAST CANCER: A CASE-CONTROL STUDY
Review round: 2
Reviewer: 2

Output:
Basic reporting: The text has been revised for continuity and additional references have been included as requested by reviewers.
Experimental design: The details of experimental design have now been explained.
Validity of the findings: The authors present a case control study which opens up direction for further investigation.
Additional comments: The authors have satisfactorily addressed the concerns raised in the review report and have made the appropriate changes


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

Input:
Title: A NEW SPECIES OF BRACHYCEPHALUS (ANURA: BRACHYCEPHALIDAE) FROM SOUTHERN BRAZIL
Review round: 1
Reviewer: 1

Output:
Basic reporting: The report is absolutely clear and certainly adheres to the standards expected in modern taxonomy and systematic biology.
Experimental design: The research problem is well defined in the context of the discovery and description of biodiversity, and the methods employed by the Authors are those needed to uncover the unknown biodiversity.
Validity of the findings: The Authors conclusively demonstrate that the organism of interest in new to science.
Additional comments: Pie and Coauthors describe a new species of Brachycephalus from southern Brazil.  The Authors have produced an outstanding, detailed description of this new taxon from phenotypical, ecological, and genealogical standpoints.  I have nothing to add except for asking one question.  In what respect is the new species remarkable?  Remarkable means "worthy of being or likely to be noticed especially as being uncommon or extraordinary".  What mechanisms, processes or the outcomes of mechanisms and processes render this new species extraordinary?  I fear that by using the word "remarkable" the Authors may have placed upon themselves the burden to justify the use of this word on scientific grounds.


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: A NEW SPECIES OF BRACHYCEPHALUS (ANURA: BRACHYCEPHALIDAE) FROM SOUTHERN BRAZIL
Review round: 1
Reviewer: 2

Output:
Basic reporting: There are numerous minor problems with the usage of the English language throughout the manuscript, especially with the usage of prepositions. The manuscript structure is good, but I suggest to delete the "conclusions" paragraph which seems superfluous.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The authors make a strong point for their suggested taxonomy including the description of a new species which is well supported by coloration, morphology, DNA barcoding data, and bioacoustics. I have made numerous minor edits and several comments/suggestions in the attached PDF. I am looking forward to seeing this work in print.


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

Input:
Title: A NEW SPECIES OF BRACHYCEPHALUS (ANURA: BRACHYCEPHALIDAE) FROM SOUTHERN BRAZIL
Review round: 1
Reviewer: 3

Output:
Basic reporting: The paper wish to describe a new species of Brachycephalus belonging to the B. pernix group and the text is mostly clear and unambiguous, yet some improvements could be made to sintax and grammar.

The authors have a tendency to cite themselves along the text, sometimes ignoring more consecrated references from various disciplines. In some cases, this is not a problem, although other cases are more problematic and were highlighted along the text.

Article structure is generally ok. However some topics need major changes (detailed in the text). Some figures have low quality and also demand adjustments, specially the photos of holotype.

The article is self-contained, yet the results presented are not enough to corroborate the hypothesis of a new species.
Experimental design: The paper is within the Aims and Scope of the journal.

The research question is well defined, relevant and meaningful.

Although the research included highly technical methods, sometimes materials and references are not enough to fulfill these analysis, which led to dubious or incomparable results. Some critical points are highlighted along the text.
Validity of the findings: Although the candidate species present some features that could distinguish it from its congeners, the overall result is inconclusive, with not enough evidence to corroborate the hypothesis of a new species.

Some of the data is robust (e.g. external morphology data), but other data require major corrections that could impact the results (e.g. bioacoustics).

Ultimately, the work's conclusion is within the scope and dialogs with the remaining text.
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: A NEW SPECIES OF BRACHYCEPHALUS (ANURA: BRACHYCEPHALIDAE) FROM SOUTHERN BRAZIL
Review round: 2
Reviewer: 1

Output:
Basic reporting: no further comments
Experimental design: no further comments
Validity of the findings: no further comments
Additional comments: The authors produced a fine revision of their work addressing the corrections and comments of the reviewers. I liked the original manuscript and am happy to see this improved revision. I am looking forward to see this work being published. Gunther Köhler


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

Input:
Title: THE EFFICACY OF VIRKON-S FOR THE CONTROL OF SAPROLEGNIASIS IN COMMON CARP, CYPRINUS CARPIO L
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript describing the safety and applicability of Virkon-S for treatment of saprolegniasis in common carp is well-written and provides sufficient background outlining the problem being studied.
Several items which may improve clarity are listed below in order of occurrence:
1.	Credit line (line 7) should include country of origin.
2.	Lines 56-58 and throughout manuscript and reference list: all formal latinized taxon names (phylum, class, order, family, genus, species) should be written in italics.
3.	Lines 57-59: make the definition of “Saprolegnia complex” and its role in disease clearer. Suggest introducing the two families within the order Saprolegniales before introducing the main genera.
4.	Line 85: reword to avoid using the phrase “secure biosecurity”.
5.	Line 106: reverse numbers to coincide with average size and weight.
6.	Line 109: was “apparent satiation” a measurable status? If so, how was it objectively measured? If not, this phrase can be deleted.
7.	Line189: after “added to” might insert “tanks containing”
8.	Line 234: no need to state “and 4 ppm is even lower than 100 ppm”.
9.	Line 291: change “flagella” to “flagellated”.
10.	Line 301: word, “species” should not be in italics.
11.	Figure 2: significant structures as described in the text are difficult to see in the figure ( germinated, un-germinated, and bulged spores). It may be useful to point these out in the figure.
Experimental design: The research question was clearly-defined and addressed an important knowledge gap. The investigation was rigorous, and of high technical and ethical standards. Method details were sufficient to allow replication by other investigators.
Validity of the findings: Appropriate controls were included and data is statistically sound. Conclusions are appropriately linked to the original research question and provide information that is immediately applicable to the aquaculture industry.
Additional comments: No additional comments


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

Input:
Title: THE EFFICACY OF VIRKON-S FOR THE CONTROL OF SAPROLEGNIASIS IN COMMON CARP, CYPRINUS CARPIO L
Review round: 1
Reviewer: 2

Output:
Basic reporting: Strengths: The manuscript presents an important fish disease and a potential treatment. The experimental plans are very well design, especially the toxicity assay. The results from these parts meet publication quality.

Weaknesses:
•	Several sentences are not clear and should require more rigorous professional English to conform to professional standards.
•	Please provide numbers of fish and replicates used in the experiments
•	The quality of figure 2 suffers from a good resolution and clarity.
•	Raw data of toxicity in fish experiment was not shared.
Experimental design: I have a major concern with the spore inhibition assay. Figure 2 is definitely not zoospores. This entire experiment needs to be re-investigate.

Line 108: acclimatization not  acclimation
Line 121: Growth on PDA for 12 days would not induce zoospores. In fact, young mycelium 3-5 days should be used to produce zoopsores.  The induction of zoospore production is triggered by starvation. In the lab setting, the sporangia induction and release of zoopspores are done by flooding.
Line 122: Please indicate, how long were the plates incubated in distilled water?
Line 124: Misspelled “concentration”
Line 127: Please provide the parameter used whenviewing with naked eye. Surface area?
Line 127: Replace “mycelia growth” with “mycelial growth”
Line 139: Replace “mycelia growth” with “mycelial growth”
Line 156: For consistency, please use the same units for antibiotic concentrations.
Line 171 and 172: Pleae clarify. How long were the fish placed in Virkon-S? How long are they in aerated water?
Lines 195 to 198: Sentences were not clear. When was Virkon-S added? 10 days after zoospore inoculation? This experimental method needs revision.
Validity of the findings: The entire experiment of spore inhibition assay needs to be re-investigate.
Fig. 3A-C: Why plate A is pink while others aren’t. Plate D looks like it has a contamination (probably replace it with a better picture)
Fig 2: with new data, zoospores and sporangia should be labelled.
Line 208: It doesn’t look like 2ppm plate is 53.8% of 4ppm. Also, 4ppm plate appears to have contamination.
Line 211: What is meant by bulging of spores? Need to show (label) that in the pictures.  Also, why should bulging happen? Is that an effect of Virkon S?
Line 223: Growth in 4D doesn’t seem ‘slight’.
Line 252 and 254 : Replace “cotton wool” with “mycelial growth” or “cotton wool-like structure”.
Line 290 to 294: These sentences are not clear. “Most of the structures observed in the samples treated with Virkon-S were not flagella. Inhibition of cyst germination by several chemicals has been reported from the well-known plant pathogenic oomycetes, Phytophthora infestance (Matheron et al., 2000). Thus, it is possible that these bulged structures were cysts that formed from the primary zoospores”

Line 291: At this magnification, it may not be possible to view the flagella.
Line 292. Misspelled “infestans”
Line 327: “colony morphology on PDA” instead of “culture on PDA plates”.
Iine 331: Use “successful treatment” instead of “complete treatment”
Additional comments: Overall, this is an interesting study, but requires professional English writing. My major concern is around the spore inhibition assay. I do not think the authors used zoospores, probably oospores, I could not tell but definitely not zoospores. The authors should pay particular attention to ensuring that the methods and figures are complete and that new results are replaced and presented in the discussion.


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

Input:
Title: THE EFFICACY OF VIRKON-S FOR THE CONTROL OF SAPROLEGNIASIS IN COMMON CARP, CYPRINUS CARPIO L
Review round: 2
Reviewer: 1

Output:
Basic reporting: This manuscript describes an important observation regarding the potential application of Vircon-S for treatment of saprolegniasis in fish. The authors have outlined the background sufficiently and the manuscript is generally well-written.
I believe that two items, not directly related to the main point of this study, should be addressed. The first is use of the word, fungus, to describe Saprolegnia. Oomycetes are not considered true fungi; use of the word fungus should at least be explained in the introduction. Secondly, the issue of spore type (zoospore or oospore) used in the study or inability to distinguish should be addressed.
Specific points
1.  line 60; remove “only”
2. lines 63-67; This lengthy sentence is not clear. It contains three points, 1) all species of Saprolegnia responsible for saprolegniasis have not yet been identified – what is this statement based on? Is it significant to this study? 2) Saprolegnia parasitica and Saprolegnia diclina are difficult to distinguish and are often referred to as the Saprolegnia complex. 3) members of the Saprolegnia complex and Achlya hoferi are the major agents that have been associated with saprolegniasis and, among them, S. parasitica is the most important (frequent?) How does major and most important differ?
3. line 77; remove “and”
4. line 78; remove first “and”
5. line 82; remove first semi-colon in parenthesis
6. line 138; change “spores suspension”  to suspension of spores or spore suspensions
7. line 168; change “mycelia” to mycelial growth
8. line 219; remove secone “white”
9. lines 236-237; There were four concentrations but only three images in Fig. 1A-C.
10. line 239; should be MFC and less than or equal to 4 ppm
11. line 253; What is in plate2E?
12. line 255; X/Y = diameter of mycelial growth
13. lines 276-277; ….which inhibited spore germination…
14. line 286; change “that it was indeed” to ‘its resemblance to’
15. line 292; remove, change or verify use of the word, zoospore, in Table 2
Experimental design: The design and technical conduct is of high quality and reproducible.
Validity of the findings: The findings included appropriate controls and are valid.
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: CLUSTERING OF FMRI DATA: THE ELUSIVE OPTIMAL NUMBER OF CLUSTERS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Grammar, style, typo:
-	line101: “the” is missing in front of “same”
-	In Results section and later, it is often not clear whether the word "cluster" refers to the data (ground truth) or the method (expected). E.g. in lines 434 and 507, I guess the latter. I recommend adding the word "expected" whenever appropriate.
-	line 407: I think ID_inter should be ID_intra. Because in Figure 2B, it is ID_intra and not ID_inter, which is discriminative. Also, V_dmin seems also quite robust (i.e. discriminative at both noise levels).

Field background:
-	The authors provide a very concise description of the fuzzy clustering.

Literature references:
-	I find it strange that no CV indices later than 2006 is considered despite developments (e.g. (DOIs): 10.1016/j.fss.2010.07.005, 10.1109/ICSSEM.2011.6081293, 10.1016/j.fss.2013.12.013, 10.1007/s00500-016-2453-y); and that there is no reference to a recent comparison study (DOI: 10.15837/ijccc.2014.3.237).

Figures:
-	Figure 6: The layout of figure 6 is very confusing an uncommon in neuroimaging literature. I recommend presenting sequential slices at the same position for all c values, as well as the SPM results. Slice locations (i.e. z-coord in MNI space) and laterality (R-L or L-R) should be also marked.
Experimental design: Research approach:
-	It is overall well designed: I would like to emphasize the rationale of using a modified version of D (Eq. 5) and the inclusion criteria for CVs (lines 213-217).
-	The interaction between fuzziness (m) and CV indices is very important; however, I found the theoretical discussion of larger m values a bit pointless, when the authors decided to stay within the limit based on the literature. I would (also) rather like to see some analysis on how robust the CV indicies within the range of m = 1.2-2.5.

Methodological issues:
-	Reslicing a data to resolution higher than the acquisition 2x2x2mm3 vs 3x3x3mm3 is unfortunately a common mistake. It unnecessarily increases the number of voxels without adding new information. It should be particularly avoided when high dimensionality and voxel redundancy are the issues.
Validity of the findings: Speculation:
-	line 523: Suggestion of spatial constraints seems to miss the fact that, although, it is true that neighboring voxels are dependent from each other; voxels far from each other might also belong to the same (perhaps not congruent) cluster, due to the functional connectivity.

Conclusion
-	line 543: Combining different CV indices is one of the most important suggestion of the manuscript! Yet, the largest part rather focuses on the (well-supported) superiority of the new CV_new, and the integrative aspects is only demonstrated by looking at the effect of c value on CV_new.
a.	Data is robust, statistically sound, & controlled.
b.	Conclusion are well stated, linked to original research question & limited to supporting results.
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: CLUSTERING OF FMRI DATA: THE ELUSIVE OPTIMAL NUMBER OF CLUSTERS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper is well written, the objectives are clear, and method/results presented appropriately. While the code for simulated data is available, there is no code to check the actual clustering, which should also be provided.
Experimental design: The overall approach is comprehensive testing many of the ‘popular’ CV along with the new one, I have no concern here.
Validity of the findings: My only issue is with testing of the fMRI data and the lack of consideration for the smooth spatial nature of the data (acknowledged in the discussion). Without proposing here to incorporate this into the clustering, I suggest 2 additional (small) analyses:
A)	Add a measure of spatial ‘isolation’ ; for instance results from the MoA data suggest maybe 3 or 4 scales / clustering levels  - could you plot along with the clustering number the  median number of isolated voxels and median cluster size in space? Say 8 clusters is what you choose as a partition, what are there spatial size and how many isolated voxels – we know isolated voxels don’t make much sense
B)	Given the data driven approach, why only comparing to the MoA auditory activation map? B.1) I suggest again for the 3/4 scales / clustering levels to correlate each cluster time course with the design to get an idea of which one follows the experimental time course B.2) check/report better on spatial structures, depending the clustering solution, we can easily interpret some cluster as motion or csf; B.3) running GIFT with infomax I got 35 components and only one fitting the design; how does that compare?. I understand the goal is not to compare to ICA, but ICA is quite popular and clustering is not despite the advantage of possibly showing hierarchical levels of segregations which is a strong ‘selling’ point, hence maybe worth comparing the maps (again say the 3 levels of clustering vs ICA)
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: CLUSTERING OF FMRI DATA: THE ELUSIVE OPTIMAL NUMBER OF CLUSTERS
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: I welcome the improvement of the manuscript and accept the authors' answers when appropriate.


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: CLUSTERING OF FMRI DATA: THE ELUSIVE OPTIMAL NUMBER OF CLUSTERS
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: Now that the additional code is provided, this makes things more transparent.
Validity of the findings: no comment
Additional comments: No additional comments


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

Input:
Title: EFFECTS OF KNEE EXTENSION WITH DIFFERENT SPEEDS OF MOVEMENT ON MUSCLE AND CEREBRAL OXYGENATION
Review round: 1
Reviewer: 1

Output:
Basic reporting: L. 57 – You stage the introduction in the manner that suggests longer repetition durations should result in greater hypertrophy, but then mention that repetition durations of 0.5 to 8 s to failure result in similar hypertrophic outcomes. This detracts from your entire purpose of this study. Do you have any theories why the study by Schoenfeld et al. (2015) observed no differences in hypertrophy across ranging repetition durations? This will to support your case for using longer repetition durations for hypertrophic changes.

L. 64 – Define “normal speed”, and “relatively low intensity”.

L. 65 – You have written that lowered peripheral oxygenation is a mechanism for muscle hypertrophy, but fail to elaborate on the mechanism itself. Please consider including more background on the actual mechanism involved here.

L. 68 to 70 – Consider the wording of this sentence for readability. It currently doesn’t flow well with words like “hence, likely, even more, thus” in the same sentence.

L. 71 – Typo: “…elicits early recruited…”

L. 72 – Does fiber type (I, IIa, IIb) play a role in the oxygenation response during resistance training?

L. 73 – Fatigue or failure?

L. 73 to 74 – It would help the reader interpret the findings in the prefrontal cortex if you provide a direction and magnitude of changes in oxygenation. In its current state, you only mention muscle oxygenation is related to changes in the prefrontal cortex.

L. 74 to 75 – What role does cerebral oxygenation play in the ability to perform maximal exercise? If anything, the current body of literature would indicate that as exercise intensity reaches maximal levels, cerebral blood flow decreases. Is this the same for oxygenation? Keep in mind that the prefrontal cortex has no role in motor control.

L. 80 to 86 – Consider removing joining words to improve paragraph readability. You have four sentences in a row starting with 1.) In fact, 2.) However, 3.) Furthermore, and 4.) Thus.

L. 82 to 84 – Please elaborate on the theory that muscle oxygenation is controlled centrally (I assume you mean from the brain).

L. 83 – Consider rewording: reduced increase.

L. 86 – Typo: missing full stop “…and blood flow (Fernandes et al., 2016) Thus…”

L. 95 to 96 – I would suggest that you are observing a response, not investigating a mechanism.

L. 180 – Typo: “…tissue thickness resulted smaller…”

L. 302 to 303 – Typo: “…In fact, difference between conditions…”

L. 320 to 322 – What are the theories for this mechanism?

L. 596 – No journal title.

L. 473, 493, 500, 509, 512, 518, 553, 557 – Find consistency with the naming of Journals (i.e. MSSE and JSCR mainly).
Experimental design: L. 146 – You have stated that 30 s of rest between RM attempts was provided to participants. Do you think this is sufficient to recovery maximal muscle force? Typical RM guidelines would lean towards 120 s to 240 s between RM attempts.

L. 201 to 204 – Based upon my own research/personal experience, performing exercise to fatigue typically causes someone to grimace, look down, look up etc. as a coping strategy. Since cerebral NIRS devices are extremely sensitive to total fluid shifts, it is important for head position to remain stable. Were participants given instruction as to their head placement during exercise?

L. 348 – Your RPE scores are not consistent with maximal performance. I would wager that a true RPE score following repetitions to concentric failure would be 10, irrespective of the repetition duration. How were the participants asked to rate RPE? Was this standardised across participants? Were participants provided any anchoring of RPE scores?
Validity of the findings: Table 1 – A table should technically be able to stand on its own. Consider listing the abbreviations in the caption (i.e. ΔHb = haemoglobin change).

Figure 1 – I assume the 10 min rest prior to the knee extension was used to collect baseline NIRS data to normalise from. If so, it’s possible that the warm-up might have influenced these values. Was there any reason why you didn’t elect to perform the warm-up after the baseline collection?

Figure 2B – Your Y axis is marked as 0 to 12, however, your RPE scale is listed as 0 to 10 in brackets. In addition, this is also inconsistent with your methodology section, where your RPE values are listed as being between 1 and 10 (L. 164).

Figure 4 and Figure 5 – Consider using graphing techniques outlined by Weissgerber et al. (2015, Beyond Bar and Line Graphs: Time for a New Data Presentation Paradigm). This will allow readers to examine the data for spread, outliers etc.
Additional comments: The authors have investigated the influence of repetition duration on oxygenation of dominant leg vastus lateralis muscle and prefrontal cortex via near-infrared spectroscopy in untrained females. To the best of my knowledge, this work is novel and adds to the existing body of evidence. The project is well designed and methodologically sound, with minor concerns. The authors have chosen appropriate statistical analyses. I find the article to be written to a satisfactory level; however, there are numerous typographical errors that could be quickly fixed to improve the overall quality of the article. I have also highlighted several areas that could be revised to improve readability. Please find my feedback below listed under line (L.) numbers. If the authors consider these changes, I would gladly recommend this article for publication in PeerJ.