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: OCCURRENCE OF MICROPLASTICS IN EDIBLE AQUATIC INSECT PANTALA SP. (ODONATA: LIBELLULIDAE) FROM RICE FIELDS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article structure is good but a paragraph on contamination control should be added. Also, the English should be improved. Literature references are sufficient.

L. 36: do you mean FTIR or µFTIR throughout the manuscript?

L. 39: treatment is not a suitable term in this context

L. 60: there are much more references, please write …e.g. Wagner…

L. 62: The English should be improved throughout the manuscript. For instance, it should be 'contaminates' here.

L. 72: 'contain' instead of 'contains'

In the file 'Raw_data_MPTs_in_edible_aquatic_insects.xlsx' there are some Thai characters/letters that cannot be understood by all readers.

Figure 3: Please, define rods.

Regarding Figure 6: what is the red spectrum and what is the gray spectrum supposed to mean? Is one of them a reference?
Experimental design: The study 'Occurrence of microplastics in edible aquatic insect Pantala sp. (Odonata: Libellulidae) from rice fields' analyses microplastic loads in the bodies of 45 (partly pooled) dragonfly larvae from Thailand. Those larvae are regularly eaten by humans.

Although it is important to gain more insight into microplastic pollution in Thailand, I recommend rejection of the manuscript. The authors are providing extremely little information on microplastics in invertebrates. They recorded 247 organisms from different taxa but only analyzed 45 (pooled) dragonfly larvae (resulting in 3 replicates each) for microplastics. The study seems incomplete and they basically analyzed 9 samples (three times 3 replicates). This is not sufficient for a valid statistical analysis. The authors also did not use any blanks/controls to test for potential microplastic contamination coming from their chemicals and they do not mention how many particles they analyzed with FTIR. Regarding FTIR, I seriously doubt that their polymer identification is correct. The substances (such as hydroxyethyl cellulose) are not reported in microplastic studies. Also, are the 4 mentioned substances (hydroxyethyl cellulose, poly(ethylene glycol) methyl ether, poly (ethylene glycol) tetrahydrofurfuryl ether, and poly (ethylene glycol) tetrahydrofurfuryl ether (methyl vinyl ether)) even plastic?
The spectra (Figure 6) are also not really clear and might be masked by residues stemming from the digested organisms. That should be looked at again.

Please, find more detailed comments below:

L. 65: microplastics can also be quickly egested by organisms

L. 131: Please provide the mean weight ± SE or SD to show that all 45 larvae had similar weights.

L. 135: When pooling the organisms, information on microplastic loads per individual gets lost. It would have been better to analyse the larvae individually. Also, that leaves you with only 3 replicates for statistics which is not enough.

L. 135: Please, add more information on contamination control. For instance, how did you avoid contaminating the dragonfly organs when dissecting the organisms?

L. 142 to 147: Did you check whether your chemical treatment would digest any microplastics? Also, a control treatment with only chemicals and no organisms seems to be missing. Such a control is essential to exclude any microplastic contamination stemming from the lab chemicals.

L. 149 and 150: Potassium formate is used to separate microplastics from sand grains but not from soft tissues.

L. 154: which sediment are you talking about since you did not take any sediment samples?

L. 154: Why did you use a plastic (nylon) membrane for filtration? That could contaminate your samples.

L. 160 and 161: Can this spectroscope be used for analyzing microscopic particles?

L. 161: How many particles were analyzed with FTIR?

L. 165: What about homogeneity of variances as an assumption for an ANOVA?

L. 256: Were there more microplastics in the gastrointestinal tracts than in the whole bodies?

L. 222 to 226 and Figure 6: I honestly doubt that polymers were correctly identified. The measured spectra are not very clear and it rather seems like there are residues (from e.g. the organisms) that disturb the FTIR measurement. Please, check that again. Also, the substances (such as hydroxyethyl cellulose) that you mention here are not really reported in any microplastic study. Also, are the 4 mentioned substances (hydroxyethyl cellulose, poly(ethylene glycol) methyl ether, poly (ethylene glycol) tetrahydrofurfuryl ether, and poly (ethylene glycol) tetrahydrofurfuryl ether (methyl vinyl ether)) even plastic?
Validity of the findings: L. 188: It is not really clear to me why the authors recorded 247 organisms from different taxa but only analyzed 45 (pooled) dragonfly larvae (resulting in 3 replicates each) for microplastics. The study seems incomplete.

L. 260 to 263: that is interesting but irrelevant for the study

I also do not agree with the authors that their study serves as a baseline since there is not a lot of data which is provided by the authors.
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: OCCURRENCE OF MICROPLASTICS IN EDIBLE AQUATIC INSECT PANTALA SP. (ODONATA: LIBELLULIDAE) FROM RICE FIELDS
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: Please see full comments in additional comments below.
Validity of the findings: Please see full comments in additional comments below.
Additional comments: General comments:
The manuscript “Occurrence of microplastics in edible aquatic insect Pantala sp. (Odonata: Libellulidae) from rice fields” provides an assessment of microplastic concentrations in an edible aquatic invertebrate widespread among rice fields in Asia. The manuscript is interesting but needs a few changes, specific comments are provided below. But generally there could be more clarity and detail in the methods to show exactly what has been done by the authors. The writing is very good and only some additional content is necessary. Another large change would be to merge the results and the discussion (or remove the references from the results). All requested changes are provided in more detail below.

Specific comments:
Abstract:
Line 27: Change MPs to MP
Line 29: This was the case a few years ago, but now there is a fair bit of information on freshwater invertebrates, I would rephrase this to say that there is a gap in understanding about pathways of MP contamination into humans (i.e., through edible insects).
Line 31: Remove “for the first time” as it does not add anything to the sentence.
Line 32: State that it is a dragonfly for the general reader’s understanding.
Line 37: Found in all organisms studied?
Line 39: Per individual per treatment? I think treatment is a confusing word here as it is not an experiment. Maybe using preparation method, or something else might be more appropriate.

Introduction:
Line 52: Comma after “environment” and before “is” on the following line.
Line 56: Briefly define primary and secondary MPs.
Line 60: I would say that this is no longer the case with a large amount of research now in freshwaters. See more recent reviews and references therein, such as: Windsor, F. M., Durance, I., Horton, A. A., Thompson, R. C., Tyler, C. R., & Ormerod, S. J. (2019). A catchment‐scale perspective of plastic pollution. Global Change Biology, 25(4), 1207-1221.
Line 64: MPs have already been defined.
Line 66: Spelling of microplastic is incorrect.
Line 72: “Contain” not “contains”.

Materials & Methods:
Line 137: Measured for what? MP concentrations?
Line 141: Were blank samples used to collect and assess airborne contamination?
Line 143: Remove “For”.
Line 158: Provide the model details for the Leica microscope. Also list the different magnifications used.
Line 162: How many scans were used to derive the spectra? What libraries were used for comparison – more detail on this method is necessary.

Results:
I recommend merging the results and discussion. At the moment there are references in the results which is not standard procedure for a paper with a separate results and discussion section. I think the easiest thing to do will be to add the current discussion to the relevant results section and create a joint results and discussion.
Line 175: It was not clear in the methods that different samples were collected during different growing periods. Add more detail to the sampling section of the methods.
Line 186: Try not to use references in the results section as this is interpretation.
Line 207: I presume these are the measurements that I was unsure about in the comment above – make this clear that the measurements for the 15 individuals were physiological/morphological
Line 211: Shouldn’t this be “MPs/replicate” not “MPs/treatment”
Line 216: This is interesting/concerning as you would expect there to be double the amount of MPs in the whole body as it includes both GT and other tissues.
Line 219: Consistent use of either microplastics or MPs throughout the manuscript.

Discussion:
See above comments on merging this with the results.


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: OCCURRENCE OF MICROPLASTICS IN EDIBLE AQUATIC INSECT PANTALA SP. (ODONATA: LIBELLULIDAE) FROM RICE FIELDS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The authors need to do some major corrections in this regard. Specifically, they need to rephrase many sentences using clear and unambiguous words.
Experimental design: There is no mention of the number of sampling sites from which the specimens were collected.
I see no relevance of the investigated water parameters in this study.
Validity of the findings: Conclusions are not well stated, especially in the abstract section.
Additional comments: Lines 206-217 should be written as a paragraph, and authors should avoid short paragraphs as much as possible.


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: OCCURRENCE OF MICROPLASTICS IN EDIBLE AQUATIC INSECT PANTALA SP. (ODONATA: LIBELLULIDAE) FROM RICE FIELDS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have made substantial changes to the manuscript based on the comments from 3 reviewers, and the manuscript is now looking much improved.

I do not have any further substantial comments, however, some minor comments are provided in the following subsections.
Experimental design: N/A
Validity of the findings: N/A
Additional comments: Line 267: This reference doesn't pertain to toxicity, it is about trophic transfer and the potential for effects across multiple trophic levels.


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: OCCURRENCE OF MICROPLASTICS IN EDIBLE AQUATIC INSECT PANTALA SP. (ODONATA: LIBELLULIDAE) FROM RICE FIELDS
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: Conclusions are not well stated.
Additional comments: This research is very timely as it would advance knowledge on MP pollution. However, I would like to request that the authors address all the annotated comments in the attached PDF and the additional comments provided below.

Abstract
1.	The goal of this study should be rephrased as follows: The goal of this study is to
assess MP contamination in an edible aquatic insect (Pantala sp.) living in rice fields.
	This is very important as there are many edible aquatic insects as alluded by the authors.
2.	The conclusion of the abstract needs to be fleshed out by mentioning the implications of the ingested MPs for human health.

Introduction
1.	Break the second paragraph of the introduction into two and merge them with the preceding and succeeding paragraphs, respectively.
Lines 62-67 should be merged with the first paragraph, while lines 68-84 should form the new second paragraph. This is necessary for a good flow of thoughts.
2.	Lines 90-94: Thoughts expressed here make it sound as if the only MP pathway to Pantala sp. is through zooplankton and smaller macroinvertebrates. I suggest that authors rephrase this section since macroinvertebrates are opportunistic feeders and they also interact directly with the water and sediment of their habitat. Microplastics can be picked up directly from water and sediment just as it is possible to ingest such through lower trophic level animals also.
Results
1.	I still do not understand the import of physicochemical water quality and the mention/list of other aquatic insects in this study. It is completely out of the scope or aim of the study. I mentioned this point in my former review. I strongly recommend that the authors expunge these aspects from the work and focus on the aim of the study. Should the authors decide to still retain this information, they will need to do a major correction on the introduction and provide a justification for water quality, other insect taxa and finally MP ingestion by Pantala sp.
2.	On the abundance of MPs among the three groups: (a) Authors could as well determine MP abundance per wet weight for the whole body, gut only, and body without gut. This could underscore the fact that guts are the reservoir for MPs in many animals (b) If the whole body recorded the highest MP abundance per individual and the body was well-rinsed with ultrapure distilled water so as to get rid of deposited MPs, this should also raise some curiosity and authors can actually suggest reasons why this was so. I know for instance that MPs have been reported in the cases (body enclosures) of caddisflies but I am not certain if they can find their way into their tissues. In the case of Pantala sp, could these MPs have been incorporated in the body integument (cuticle)? I think this is a big research problem that authors should not ignore in this study. It could be a part of the recommendation.

Conclusion
This should be re-written.
(1)	Lines 276-277 is not within the scope of this study. The study only quantified MPs in Pantala sp., it did not establish a nexus between MPs and freshwater toxicity.
(2)	Line 278-279 should also be rephrased.


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: DETECTION OF MICROPLASTICS IN LITOPENAEUS VANNAMEI (PENAEIDAE) AND MACROBRACHIUM ROSENBERGII (PALAEMONIDAE) IN CULTURED POND
Review round: 1
Reviewer: 1

Output:
Basic reporting: In this work, the authors investigated the occurrence of microplastics in Litopenaeus vannamei (Penaeidae) and Macrobrachium rosenbergii (Palaemonidae) in cultured ponds of Thailand. Incidence of microplastics in two economically important shrimp and prawn species was examined. A good attempt but there are many works carried out like this in recent times.
Experimental design: The authors have reported the MPs in the gut of prawn and shrimp of polyculture pond without emphasizing on the source profiling incidence in other body parts. Methodology, results, discussion and conclusion is ambiguous and instead of male and female prawn, incidence in different sizes could be done.
Validity of the findings: English should be improved; several grammatical mistakes have to be taken care of. Flow can be improved. Discussion has to be improved heavily. Refer more studies regarding the abundance of MPs in aquacultured organisms and pond water as very few works are cited.
Additional comments: Specific comments:
1)	L 33-35, 49, 51, 156, 165 so on: Please improve clarity of writing, the entire manuscript have to be re written.
2)	L 47: widely accepted size range of microplastics is 1 micron to 5 millimeters (please refer Mallik, A., Xavier, K.M., Naidu, B.C. and Nayak, B.B., 2021. Ecotoxicological and physiological risks of microplastics on fish and their possible mitigation measures. Science of The Total Environment, 779).
3)	L70 : State proper reason why they are more prevalent in aquatic organisms
4)	L97 : expand GT Shrimp
5)	L124: Both the times it is mentioned female freshwater prawns. Please correct
6)	L187: please mention the processing condition of shrimp and prawns of Thai supermarkets and fresh markets
7)	L159-160 – Refer mouth sizes of vannamei and rosenbergii. Please elaborate what could be the reason for significant variation in abundance, sizes, colours of MPs in these both
8)	L223: try to elaborate effects of consuming MPs (please refer Ecotoxicological and physiological risks of microplastics on fish and their possible mitigation measures. Science of The Total Environment, 779  and  Microplastics in shrimps: a study from the trawling grounds of north eastern part of Arabian Sea Environmental Science and Pollution Research 28: 48494–48504 http://doi.org/10.1007/s11356-021-14121-z)
9)	L215- Very few MPs were subjected to chemical characterization as more than 3000 MPs were reported
10)	L245- irrelevant and incorrect statement
11)	 L246: conclusion part doesn’t reflect any of the findings and moreover very ambiguous


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: DETECTION OF MICROPLASTICS IN LITOPENAEUS VANNAMEI (PENAEIDAE) AND MACROBRACHIUM ROSENBERGII (PALAEMONIDAE) IN CULTURED POND
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript describes the novel findings of the presence of MPs in the giant freshwater prawn (Macrobrachium rosenbergii) and white leg shrimp (Litopenaeus vannamei) from culture farms in Thailand. As the importance of MPs in aquaculture products (especially in crustacean products) are underestimated, I think this manuscript is worthy to be published in PeerJ. I have several concerns as belows:
Experimental design: 1. The authors have described that the shrimp and prawn samples were collected from the polyculture pond. Then, are the collected samples were from single polyculture pond? or combined from more than two pond? Needs to be clarified.
2. If available, please describe the information on the plastic devices and conditions of the sample-collected pond.
Validity of the findings: 1. Based on the manuscript of the authors, the shrimp and prawn samples were collected from culturing farms. However, in the discussion section, the authors have stated that 'It's the first study to demonstrate the presence of microplastics in commercially marketed shrimp and prawns.' (Line Nos 190-191). Which is correct? Needs to be clarified.
2. If the two target shrimp and prawn species were collected from same culture farm or pond, the authors may need to discuss why the majority of microplastics found in gastrointestinal tracts of the two species were differed in this study. Please add some discussion in the section.
Additional comments: Table 2 and Table 3 those attached in the end of manuscript should be rearranged.
The quality of Figure 1 needs to be improved.


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

Input:
Title: DETECTION OF MICROPLASTICS IN LITOPENAEUS VANNAMEI (PENAEIDAE) AND MACROBRACHIUM ROSENBERGII (PALAEMONIDAE) IN CULTURED POND
Review round: 1
Reviewer: 3

Output:
Basic reporting: This study is on microplastics- a widespread pollutant in the 21st century. The topic is very relevant, with multiple implications in aquatic ecosystems.
Experimental design: The topic is well introduced but short, so the authors can consider lengthening the introduction. The section: contamination control is missing from the methods. It would be good to elaborate on the specific measures taken to reduce surrounding contamination of mps during sampling processing.
Validity of the findings: no comment, the results are valid
Additional comments: I have some specific comments:

Line 46- microplastics are not only from 1-5 mm, they are pieces smaller than 5mm, kindly make the change.

Line 50- please include an example size of microbeads to elaborate on the point

Line 55- kindly change “inappropriate” to “improper”

Line 61- please include some examples of the effects of mp ingestion in the organisms

Line 62- abrupt change of topic, kindly include linking statements to the previous paragraph.

Line 65- include some relevant examples of pollution/deterioration etc etc. more elaboration can be included in this paragraph

Line 71- what do you mean by “consumers”?

Line 74- please elaborate on the statement that food can be a source of mps in humans

From the results section: kindly change all mentions of general name of the prawn to the scientific name for standardisation purposes

The authors can add a table in the discussion comparing the abundances of mps in other form of shrimp around the world


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: ANTIVIRAL DRUG DISCOVERY BY TARGETING THE SARS-COV-2 POLYPROTEIN PROCESSING BY INHIBITION OF THE MAIN PROTEASE
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is written very well.  The concepts are clearly defined.
English language of the manuscript is fine.
Introduction and background are good enough to present the work of the manuscript.
Experimental design: The authors have given sufficient details of the methodology in the manuscript.
Methods can be repeated to follow the results.
Validity of the findings: Research of this manuscript was done computationally,   and authors have supported theirs finding by experimental work which is a strength of this manuscript.
Additional comments: GENERAL  COMMENTS
The following are my comments which are needed to be solved before publication.
Abstract-
1-Line 20.
“To date, no new drug or vaccine has been approved for treating SARS
CoV-2 infections”
Remove “Vaccine”
2-Line-72-73. How did the authors collect a total of 37060 compounds dataset,  write in detail so readers can follow your work?
3-Line    86
Docking of all compounds was by Schrodinger glide docking module.
Correct  above sentence   by adding  “verb”.
4-Line 88.
“Compounds with docking score of -8.00 or higher were retrieved”
What was basis  to choose “ -8.00 or higher”?
5- In Line 89 -90,  Add   x y and z  coordinates.
6-Line 100,  correct  50ps  , it should be  50 ps.  Check  for  such errors.
7-Line 114 ,  add  reference for  “g_mmpbsa tool”.
8-  Figure 1 , A. B, C, and D   remove the black background.   Improve picture quality.
9- Figure 5,  Correct  scale of X-axis ( It should  be maximum 100 ns  but   it is 100000 ns)
10-  Since authors have performed experiment by  using   SARS-CoV-2  virus.   Add an approval of bioethics statement to conduct the experiment by using live virus.


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: ANTIVIRAL DRUG DISCOVERY BY TARGETING THE SARS-COV-2 POLYPROTEIN PROCESSING BY INHIBITION OF THE MAIN PROTEASE
Review round: 1
Reviewer: 2

Output:
Basic reporting: The presented work seeks to discover antiviral compounds which may be candidates for treating COVID-19. The question of which drug treatments might improve patient outcomes in COVID-19 is the subject of ongoing research in the field. The presented work follows a valid investigation and contributes a result towards that research effort.

The article is written with clear English. There are some minor mistakes with spelling and grammar which do not substantially affect the article's content. There is an issue with the capitalisation of some proper nouns in the article, such as "glide" (referring to the docking software "Glide"), "protein data bank" ("Protein Data Bank"), and so on. On lines 102-103, the sentence "production stages were done over simulation times of 20 and 100 ns with NPT ensemble was adopted" is confusing, and on line 104 "algorithmfor" is missing a space. There should be a space between numbers and their units, such as in "50ps" ("50 ps") or "300K" ("300 K"). Although these are minor issues, the authors should consider double-checking the prose in order to improve the readability of the article.

The introduction adequately describes the motivation for the research. However, the section does not support or contextualise the in vitro screening part of the study, despite this being crucial to its core output, which is the 37% reduction of replication after 48 hours demonstrated for Birinapant. The authors should expand the introduction to the article to make clear the importance of the in vitro assay to produce evidence for establishing a candidate treatment. The Introduction section also lacks a sufficient review of similar in silico / in vitro screening studies aimed at drug / antiviral repurposing, so such a review should be undertaken and added.
Experimental design: The authors have chosen to undertake in silico screening first, followed by an in vitro screen for the best-scoring compounds, and this is a standard approach for drug repurposing. The two stages of docking and the stage of molecular dynamics have been described well.

Neither the section "Construction of drugs and compounds dataset" beginning line 71, nor the referenced Table 1, describes the fingerprint or structure similarity methods used to create the compound library. This section must be made more detailed. There are three questions which should be answered: what were the seed compounds of the search (known antivirals), how were compounds generated to be tested against those seeds, and which methods were used to assess compound similarity?

On line 72 and in Table 1, it is written that a set of 37,060 compounds were tested, but in Supplementary File 1 ("SP docking results") 47,068 results are listed. No subsequent references to Supplementary File 1 explain the discrepancy. The authors should describe more clearly the dataset that is being presented in Supplementary File 1. Which 47,068 compounds were used?

Vero E6 is an appropriate cell line for this kind of SARS-CoV-2 infection study. The provenance is described as the Korean Cell Line Bank in the subsection "Cell line and virus" beginning on line 116. The authors' description is missing an account of how the cell line has been authenticated and checked by the authors for possible contamination, which should be part of the quality control process for this experiment [DOI:10.1023/A:1022949730029, DOI:10.1038/bjc.2014.166]. The same subsection outlines that the SARS-CoV-2 sample used by the authors was NCCP No. 43326. The authors may wish to insert a sentence to clarify that viral samples based on NCCP No. 43326 are the wildtype virus, i.e. GISAID clade S, PANGOLIN lineage A. Variants of SARS-CoV-2 are of pressing importance, and the wildtype is no longer the most relevant strain to the COVID-19 pandemic, so explicitly mentioning the lineage used in the experiment will help clarify the applicability of the research.
Validity of the findings: The in silico portion supports prior in silico investigations regarding the antiviral drug Birinapant, which conclude it has the potential to limit the replication of SARS-CoV-2 by inhibiting Mpro [DOI:10.1080/07391102.2020.1805019]. The in silico work also highlights Atazanavir, for which there are also ongoing investigations [DOI:10.1101/2020.04.04.020925, DOI:10.1186/s13063-020-04987-8]. The in vitro validation focuses on these two drugs and presents a positive result for Birinapant inhibiting the replication of SARS-CoV-2 in the Vero E6 cell line at 10 μM after 48 hours.

In lines 19-20 of the abstract, a claim is made that "no new drug or vaccine has been approved for treating SARS CoV-2 infections". The antiviral drug Remdesivir has already been approved for the treatment of COVID-19 (e.g. by the MHRA in the UK), which followed the results of the ACTT-1 trial last year [DOI:10.1056/NEJMoa2007764]. Monoclonal antibodies have also recently been approved (e.g. by the MHRA) as a treatment for COVID-19 [DOI:10.1136/bmj.n2083]. There are also now clearly many approved vaccines which are efficacious at preventing COVID-19. The statement appears to be severely outdated and must be updated to reflect the current state of research into treatments for COVID-19.

In line 36 of the abstract, it is claimed that "Birinapant can be used to treat COVID-19." This is a strong claim which is not adequately supported by the experimental result presented, which is a 37% reduction of replication in an in vitro assay based on the Vero E6 cell line. Claims that something is a treatment should be supported by clinical evidence. In the case of this research, it would be more accurate to conclude that Birinapant is a candidate for further investigation in order to establish whether it is an effective treatment. A similar point is made in the Discussion section on lines 270-271, saying "Birinapant's anti-SARS-CoV-2 activity supports its usage as an anti-COVID-19 medication", and this should also be updated to say e.g. "...supports further investigation into its usage...".

The results of the docking and molecular dynamics stages of the study are well-presented and sufficient raw datasets for those stages have been provided in the supplementary information.

The caption for Figure 7 lists the concentration tested as 10 mM, which is also present in lines 128-129 of the Methods section. However, a value of 10 μM is written in the abstract as well as in the "SARS-CoV-2 Plaque inhibition assay" subsection of the Results section. The value tested was presumably 10 μM, as per similar studies, so the authors should clarify or correct the "10 mM" values. This subsection refers to "Fig. 6", but it seems the matching figure would be "Fig. 7". Furthermore, it would be helpful for the authors to supply a table of raw data for Figure 7 in the supplementary information.

On line 230, it is stated that "the estimated IC 50 values for birinapant was 18±3.6 µM." It must be stated, possibly in the Methods section, how this value is estimated, and any further raw data that is relevant should be provided in a figure in the main text and in a table in the supplementary information. Can the authors produce a dose-response curve to support the asserted value? The value should then be related to comparable values in other in vitro COVID-19 replication inhibition studies, such as to Remdesivir in Vero E6 cells [DOI:10.1016/j.antiviral.2020.104786].

The Discussion section does not mention important context from the field for the two compounds that were primarily investigated, Birinapant and Atazanavir. Birinapant was highlighted last year by an in silico study following a similar method of docking then molecular dynamics [DOI:10.1080/07391102.2020.1805019]. The authors should relate their work to this earlier study - the in silico part supports its conclusions, and the in vitro work extends the evidence for the candidacy of Birinapant for further work. Atazanavir has also been the subject of a mixed in silico / in vitro investigation [DOI:10.1128/AAC.00825-20]. Like in this work, it was found by Fintelman-Rodrigues et al. that Atazanavir undergoes stable binding with a strong binding energy to Mpro. However, the Fintelman-Rodrigues study found that Atazanavir exhibits antiviral activity in Vero E6 cells in vitro, and then goes on to establish that the inhibition of replication holds in human cells. The disagreement between this work and the in vitro part of the Fintelman-Rodrigues study should be discussed, particularly in the context of upcoming clinical trials involving Atazanavir [DOI:10.1186/s13063-020-04987-8].
Additional comments: The core research behind this work, in which Birinapant is selected in silico from a large panel of compounds and then its activity verified in vitro, is promising. However, the article would need major revision in order to fully describe the work done and to contextualise its place within the current body of literature. Particularly, there are methods used which have not been described; the authors have not related the work to any relevant developments in COVID-19 therapeutics over the last year, including comparable in silico and in vitro studies; and some of the stated discussion and conclusions of the study are not supported by the results generated.


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: ANTIVIRAL DRUG DISCOVERY BY TARGETING THE SARS-COV-2 POLYPROTEIN PROCESSING BY INHIBITION OF THE MAIN PROTEASE
Review round: 1
Reviewer: 3

Output:
Basic reporting: “To date, no new drug or vaccine has been approved for treating SARS CoV-2 infections” – In fact there are many vaccines that have been approved and a host of new drugs are in development. This is clearly a naive statement that should be revised.

Generally, the authors do not acknowledge the work of other groups in this area. For example, birinapant has been identified by other studies of a similar nature to that submitted by the authors but these are not cited.

e.g.
https://www.tandfonline.com/doi/full/10.1080/07391102.2020.1805019
https://www.tandfonline.com/doi/full/10.1080/07391102.2020.1768151

I feel that many of the compounds identified in this study have been identified by others with a similar or identical approach - the authors do little to recognise this.
Experimental design: The experimental design appears to be sound and the plaque assays are an important addition.
Validity of the findings: The paper is clearly written and the findings of the paper are generally supported by the data presented.
RMSD and gyration figures are very difficult interpret and should be separated. E.g. Fig. 5. the data for birinapant is barely visible.
Additional comments: Generally, this is a useful addition to the SARS-CoV-2 molecular docking repurposing genre, especially since the wet lab data is included. I feel that many of the compounds identified in this study have been identified by others with a similar or identical approach - the authors do little to recognise this.


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

Input:
Title: CHARACTERIZATION OF THE BARK STORAGE PROTEIN GENE (JCBSP) FAMILY IN THE PERENNIAL WOODY PLANT JATROPHA CURCAS AND THE FUNCTION OF JCBSP1 IN ARABIDOPSIS THALIANA
Review round: 1
Reviewer: 1

Output:
Basic reporting: This report is well written with professional English used throughout. It is well structured and self-contained.
Experimental design: Research questions were well defined, relevant & meaningful. Experiment designs were appropriate.  Methods and materials were sufficiently described.
Validity of the findings: Meaningful replications were included to support the findings, which are generally robust and statistically sound.
I commend the authors for the extensive and pioneer work on the Jatropha bark storage protein that may play an important role in nitrogen cycling in this important biofuel crop.
Additional comments: The reviewer has some comments/suggestions for further improvement:
1.	Creating a better link to Jatropha in the tropical climate: The authors investigated Jatropha defoliate in autumn and dormancy in wintertime somewhere in China. Jatropha is mostly grown in the tropics as a perennial that sheds off leaves during drought periods. It would be important to link the season change-related protein-related mobilization to possible drought-related protein mobilization.
2.	JcBSP1 has a seasonal RNA transcript pattern consistent with season-related total protein concentration change. Authors suggest that JcBP1 might play an important role in seasonal nitrogen cycling. The conclusion will be better supported with the quantification of JcBP1 in the total protein. A high percentage would better support the suggested ‘important role’.
3.	Among the 21 transgenic Arabidopsis lines for over-expression JcBSP1 under the constitutive strong 35S promoter, two of them showed higher JcBSP1 transcripts and larger rosette leaves and flowers, also larger seeds. These phenotypes suggested the involvement of JcBSP1 in plant growth and development, not exactly expected for a balk storage protein. It is necessary to exclude the possibility of pleiotropic phenotypes caused by insertion mutagenesis or multiple transgene insertions. Some molecular characterization of transgene copy number and insertion sites for these two lines would be very helpful.


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

Input:
Title: CHARACTERIZATION OF THE BARK STORAGE PROTEIN GENE (JCBSP) FAMILY IN THE PERENNIAL WOODY PLANT JATROPHA CURCAS AND THE FUNCTION OF JCBSP1 IN ARABIDOPSIS THALIANA
Review round: 1
Reviewer: 2

Output:
Basic reporting: In the paper " Characterization of the bark storage protein gene (JcBSP) family in the perennial woody plant Jatrophacurcas and the function of JcBSP1 in Arabidopsis thaliana", the authors identified six members of JcBSP gene family in J. curcas genome. Thepatterns, seasonal changes, and responses to nitrogen treatment in gene expression of JcBSPs were detected by qRT-PCR. Moreover, JcBSP1 was overexpressed expressed in Arabidopsis resulted in a phenotype of enlarged rosette leaves, flowers, and seeds, and significantly increased the seed weight and yield in transgenic plants. This study laid the foundation for further research on the function of BSP genes in the plant growth and development.

（1）In this manuscript, the JcBSP1 from Jatrophacurcas was expressed in Arabidopsis to verify JcBSP1 function. So, the authors described that “JcBSP1overexpression in Arabidopsis…..”, which might be not accurate.

（2）Is there any homologous genes of JcBSP1 in Arabidopsis thaliana? Does the authors checked that or any literature reported?

（3）In Figure 7B, the X-axis is better simplified as “……(week)”, and uniform the unit of Y-axis as in Figure 9 B and C.

（4）Standard deviations in Figure 8B about qRT-PCR is very big, please more repeats to confirm these results.
Experimental design: This study was well-designed, and the experiments were performed properly.
Validity of the findings: The article is well-drafted, and include sufficient literature references.
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: CHARACTERIZATION OF THE BARK STORAGE PROTEIN GENE (JCBSP) FAMILY IN THE PERENNIAL WOODY PLANT JATROPHA CURCAS AND THE FUNCTION OF JCBSP1 IN ARABIDOPSIS THALIANA
Review round: 2
Reviewer: 1

Output:
Basic reporting: This report is well written with professional English used throughout. It is well structured and self-contained.
Experimental design: Research questions were well defined, relevant & meaningful. Experiment designs were appropriate. Methods and materials were sufficiently described.
Validity of the findings: Meaningful replications were included to support the findings, which are generally robust and statistically sound.
I commend the authors for the extensive and pioneer work on the Jatropha bark storage protein that may play an important role in nitrogen cycling in this important biofuel crop.
Additional comments: The reviewer gave some comments/suggestions for further improvement after the 1st review. These questions are well addressed in the revision.


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

Input:
Title: CHARACTERIZATION OF THE BARK STORAGE PROTEIN GENE (JCBSP) FAMILY IN THE PERENNIAL WOODY PLANT JATROPHA CURCAS AND THE FUNCTION OF JCBSP1 IN ARABIDOPSIS THALIANA
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors addressed all the questions that I raised. I have no more questions now.
Experimental design: The authors addressed all the questions that I raised. I have no more questions now.
Validity of the findings: The authors addressed all the questions that I raised. I have no more questions now.
Additional comments: No additional comments


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

Input:
Title: CROSS-SECTIONAL STUDY OF CHROMOSOMAL ABERRATIONS AND IMMUNOLOGIC FACTORS IN IRAQI COUPLES WITH RECURRENT PREGNANCY LOSS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Please see my additional comments.
Experimental design: Please see my additional comments.
Validity of the findings: Please see my additional comments.
Additional comments: The manuscript entitled “Cross-sectional study of chromosomal aberrations and immunologic factors in Iraqi couples with recurrent pregnancy loss” by Doaa A. Khamees et al. investigated the chromosome abnormalities and immunological factors using peripheral blood from 25 couples with more than two RPL in the first trimester from Iraq in comparison to 25 healthy females. They performed Karyotyping to detect structural abnormalities and ELISA to measure Anticardiolipin (IgG and IgM), antiphosopholipid (IgG and IgM), lupus anticoagulant, and IL-6. They have found that chromosomal abnormalities were prevalent in 28.0% of RPL couples, while control females had no chromosomal abnormalities. Immunological factors were not significantly differential between RPL and control group. The study is of potential significance and emphasizes the importance to conduct karyotyping in patients with RPL.
1.	In Text Line 102, “This cross-sectional descriptive study was done on 25 couples (50 individuals) who had a history of more than two abortion during the first trimester and 25 healthy females without a history of abortion as the control group”. What are the inclusion criteria of control women?
2.	Table 1 was not described and interpreted in the manuscript. It showed that distribution of healthy and RPL women was similar in different age ranges (P-value>0.05 in >28 years). Authors could present the data using stacked bars, which is straightforward.
3.	Figure 1 demonstrated that the number of abortion was increased with the age progression at which a moderate positive significant correlation was seen”. Is it just because older women tried more pregnancies (thus more miscarriage) than younger women?
4.	In text line 170, “Case 1 was a 36 years old female with history of two babies born with Down syndrome and repeated miscarriage”. It should be “36-year-old female”.
5.	How will the aberrant karyotypings in the manuscript guide clinical decision? If patients are diagnosed to bear aberrant chromosomes that induce RPL, what is the clinical suggestion?
6.	Did authors measure anti-phospholipid (IgG and IgM), anti-cardiolipin (IgG and IgM), lupus anticoagulant, and IL-6 in healthy women? Are the levels in RPL women significantly higher than healthy women?
7.	In addition to immunological factors above, other diagnostic parameters were also reported to differ between RPL patients and healthy women, including NK-cells (PMID: 24285824, PMID: 21613313), Treg (PMID: 19766059, PMID: 20331584), dendritic cells, plasma cells, and human leukocyte antigen (PMID: 18263639). Are they differentially expressed in RPL patients compared to control group in the manuscript?


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

Input:
Title: CROSS-SECTIONAL STUDY OF CHROMOSOMAL ABERRATIONS AND IMMUNOLOGIC FACTORS IN IRAQI COUPLES WITH RECURRENT PREGNANCY LOSS
Review round: 1
Reviewer: 2

Output:
Basic reporting: There are many grammatical mistakes throughout the manuscript, the authors should proofread and seek help form professional editors.
Experimental design: 1. The authors need to increase the sample size to reach solid conclusion.

2. The authors should chose a comparable number of participants in each age range in the studied and control group. The number of the participates younger than 28 and older than 34 are quite different between the two groups.

3. Instead of using 25 women with no history of abortion as control group, the authors should also include and do karyotype analysis on their male partners.
Validity of the findings: 1. The authors should deleted the 5 cases of female with abnormal karyotypes from the correlation analysis in figure 1 since the recurrent pregnancy loss in these women is mainly caused by their chromosomal mutations but not age.

2. This reviewer is confused by "All of the above values were lower than those observed for the cut-off values and considered negative for these parameters" in line 202-203 and "The results revealed......were in normal ranges in both RPL and control groups" in line 286-288 and thought these conclusions are in conflict with each other. The authors should provide the normal range for all immunological factors measured in the study as part of table 3.

3. The authors can not just conclude no differences between the two groups on all immunological factors without showing the statistical analysis results to the readers.

4. In line 217, the  should be 24% (n=6/25) in this study.

5. In line 218, the chromosomal abnormalities should be 20% (5/25) in female and 8% (2/25) in males.

6. In line 263, the prevalence rate should be 12%
Additional comments: The authors should summarize the findings from current available studies on RPL in Iraq couples and/or those from other regions and include a table that lists all important factors such as age range, number of abortion, karyotype abnormality rate, etc to help readers better understand and appreciate the value of this study. In the current discussion, the authors were merely stating that their numbers are lower or higher than other studies without any insightful analysis on the possible reasons for these differences. Since the authors purposely chose women with more than 3 abortion, their chromosomal abnormality could be higher than those with less than 3 abortions in other studies, but without providing these information, the readers wouldn't know. These also applies to the immunological factor analysis, a table that summarized those parameters in available studies should make this one more valuable and meaningful.


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: CROSS-SECTIONAL STUDY OF CHROMOSOMAL ABERRATIONS AND IMMUNOLOGIC FACTORS IN IRAQI COUPLES WITH RECURRENT PREGNANCY LOSS
Review round: 2
Reviewer: 1

Output:
Basic reporting: Authors have successfully responded to all my comments.
Experimental design: None.
Validity of the findings: None.
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: USING VIRTUAL REALITY FOR ANATOMICAL LANDMARK ANNOTATION IN GEOMETRIC MORPHOMETRICS
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1. The authors should make the result section more concise and discuss the results only in discussion section. In current form, the result section is too long and hard to follow.
2. The figure 2 is hard to understand, there is too many points and the colours are not well perceived. I suggest simplifying the figure. Do the regression lines suggest learning effect?
3. Statistical significant differences in figure 3, 4, 5 should be indicated in the figures.
Experimental design: 1. The number of included operators is low. This should be emphasized in discussion section.
2. When annotating with traditional system, did authors use the simultaneous view three perpendicular cross sections?
Validity of the findings: 1. The authors included only four operators which significantly limits the generalizability of their findings.
Additional comments: 1. The authors included a video of virtual reality system in the supplement. Can a short video/figures of the traditional system using 2D display and mouse and keyboard also be provided? This would allow readers that are not familiar with such system to better understand it.
2. Could the accuracy of annotation using virtual reality be improved if using haptic device that enables precise movements and has six degrees of freedom, instead of using classical VR controller with power grip.
3. In your virtual reality, is it possible to also “look” through the model and look at its cross section? Could such view improve the landmark recognition and annotation accuracy?


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: USING VIRTUAL REALITY FOR ANATOMICAL LANDMARK ANNOTATION IN GEOMETRIC MORPHOMETRICS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors present a study comparing two systems for annotating landmarks on 3D models, in this case seal skulls. One is a virtual reality system that uses a stereoscopic headset, the other is a conventional system with a monitor and mouse. The topic is of some interest and the manuscript is well written with good illustrations and adequate references. However, the title of the manuscript is quite general. It should describe the content a little more precisely. In Fig. 3, the positions of the magnified details in the images of the skulls should be marked.
Experimental design: It remains unclear why the resolution of the 3D model was also reduced for the measurement with the Stratovan Checkpoint software. This may not take into account an important advantage of this method.
Validity of the findings: To put the accuracy achieved into perspective, the resolution of the 3D models studied should also be provided in physical units. For this purpose, e.g. the mean distance of the vertices of the model could be given.
In my own experience, wearing a VR headset for extended periods of time can be quite exhausting. The authors should address the issue in the discussion.
Additional comments: The authors write "Procrustes distance is defined as the sum of distances between corresponding landmarks of two aligned shapes". Various definitions of the Procrustean distance exist. The authors may want to check if this describes the version used in the "geomorph" package.


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: USING VIRTUAL REALITY FOR ANATOMICAL LANDMARK ANNOTATION IN GEOMETRIC MORPHOMETRICS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The paper has a clear aim and objectives but suffered from no ground truth to support their analysis on accuracy. Also there are several issues need to be clarified.
Experimental design: There are several issues in the paper which are needed to be clarified:
1. There is no ground truth in the study that no evidence to support that the VR is more accurate.
2. Type 2 and 3 outliers should be replaced and at least the authors needs to show the results without replacing outliers.
3. 6 landmarks of 6 skulls and marked 6 times of each landmarks on 2 systems, it would be 432 rather than 288 landmark configurations; and its is not clear that how the authors handle the repeated measurements.
4. It is not clear how the mean landmarks were calculated.
5. Why GPA instead of Partical Procrustes Analysis (PPA) was used to assess the measurement errors? I think that the Procustest distance was scaled down by the centroid size.
Validity of the findings: VR for landmarking has been promoted for three decades but its benefits were limited in clinical practices. The study did not have ground truth to support the analysis that it is not reliable to state that VR is more accurate (maybe it is true).
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: USING VIRTUAL REALITY FOR ANATOMICAL LANDMARK ANNOTATION IN GEOMETRIC MORPHOMETRICS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors satisfactorily adressed all my objections.
Experimental design: The authors satisfactorily adressed all my objections.
Validity of the findings: The authors satisfactorily adressed all my objections.
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: USING VIRTUAL REALITY FOR ANATOMICAL LANDMARK ANNOTATION IN GEOMETRIC MORPHOMETRICS
Review round: 2
Reviewer: 2

Output:
Basic reporting: In my opinion, the authors have adequately addressed the issues mentioned.
Experimental design: No commment
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: USING VIRTUAL REALITY FOR ANATOMICAL LANDMARK ANNOTATION IN GEOMETRIC MORPHOMETRICS
Review round: 2
Reviewer: 3

Output:
Basic reporting: no comment
Experimental design: Partial Procustes Analysis should be used instead of General Procurstes Analsysis since there should be no scale but only rotations and translations in the shape aligning or calculating the mean shape. Scaling in General Procustes Alignment would change the size of the shapes to be aligned.
Validity of the findings: The authors did not address the issue of the repeated measurements. The repeated data sampled from the same sample 6 times were correlated.
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: MICROPROPAGATION OF POKEWEED (PHYTOLACCA AMERICANA L.) AND COMPARISON OF PHENOLIC, FLAVONOID CONTENT, AND ANTIOXIDANT ACTIVITY BETWEEN POKEWEED CALLUS AND OTHER PARTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Title : In vitro propagation, chemical constituents and antioxidant activity from different explants of Phytolacca americana L.
Q1 : It is necessary to bring out the work aim which is the comparison between the phytochemical content at callus level and at other plant part level.
Abstract :
“Factors affecting callus induction and direct shoot organogenesis were investigated and compared with total phenolic content (TPC), total flavonoid content (TFC) and total antioxidant activity. Four different explants were cultured on MS medium containing various concentrations of 2,4-D and IBA”.
Q1: This paragraph does not reflect the adopted methodology
 “This is the first report describing comparative micropropagation using chemical constituents and antioxidant activity from different explants of pokeweed. Results will provide significant information to further enhance bioactive compound contents of pokeweed calli using elicitation methods.
Q2: This paragraph should be reformulated. It is not clear.
Experimental design: Materials and methods:
Q1 : Line 78 : Rinsing has been carried out for how long?
Q2 : Line 88 : while describing the callus induction, the concentrations (1,2, 3 and 4 mg / l) are for which hormone, 2,4-D or IBA? It is not clear. Likewise, for line 100.
Q3 : Line 89 : What are the callus culture conditions (Photoperiod)?
Q4 : Line 105 : what is the callus origin used for the chemical constituents determination ? Why you did not perform the assays using the same explants used for callus induction.
Q5 : Line 95 et 105 : At what temperature the callus were dried ? 70 ° C or 45 ° C?
Q6 : Line 107 : At what temperature the sonication was performed ?
Validity of the findings: Results
Q1 : The direct organogenesis work is interesting, but these are only preliminary tests. Rooting tests could be done to value this work. Besides, it is quite normal that the rooting rates are zero since you only used cytokinins.
Q2: There is a lack of a connective link between the different parts of the work. The insertion of the direct organogenesis part is not done in a proper way.

Q3 : In order to achieve callogenesis induction, why you did not try the auxin and cytokinin combination?
Q4 : Line 127 : You argued in part MM that the antioxidant activity is calculated as a percentage : Free radical scavenging activity was calculated by the following equation : % free radical scavenging activity by DPPH = [1-(A sample / A control)] x 100. In table 3, the results are presented only in IC50 by DPPH assay (µg / ml).
Additional comments: Discussion :
Chemical constituents and antioxidant activity: This part needs to be further improved and amended with more recent references. The authors should place more emphasis on the work done on the extraction and assay of bioactive molecules from tissue cultures.


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: MICROPROPAGATION OF POKEWEED (PHYTOLACCA AMERICANA L.) AND COMPARISON OF PHENOLIC, FLAVONOID CONTENT, AND ANTIOXIDANT ACTIVITY BETWEEN POKEWEED CALLUS AND OTHER PARTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Refer attachment.
Experimental design: Some methods used need revision. Refer attachment.
Validity of the findings: Refer attachment.
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: MICROPROPAGATION OF POKEWEED (PHYTOLACCA AMERICANA L.) AND COMPARISON OF PHENOLIC, FLAVONOID CONTENT, AND ANTIOXIDANT ACTIVITY BETWEEN POKEWEED CALLUS AND OTHER PARTS
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: After reading the second version of the paper “ Micropropagation of pokeweed (Phytolacca americana L.) and comparison of phenolic, flavonoid content, and antioxidant activity between pokeweed callus and other parts '' I find that the authors have answered to all clarifications and have answered to all requested changes.
Thus, I believe that their study deserve to be published.


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: INTERPRETATION OF EXERCISE-INDUCED CHANGES IN HUMAN SKELETAL MUSCLE MRNA EXPRESSION DEPENDS ON THE TIMING OF THE POST-EXERCISE BIOPSIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: •	The subheading “Conclusions” needs to be added to the Abstract
•	Lines 59-82: Obviously there are many, many studies with measurement of post-exercise mRNA expression and a good cluster of them are referenced here, but to imply that there is a dearth of those that go beyond the first 24 hours, or that few have more than 2 or 3 timepoints is not a fair representation of the literature in my opinion. For example, the following (not exhaustive list) could be said to be exceptions to the points you make, granted some are resistance exercise.
o	Pilegaard et al 2005 https://pubmed.ncbi.nlm.nih.gov/16092055/
o	Schmutz et al 2006 https://pubmed.ncbi.nlm.nih.gov/16362354/
o	Louis et al 2007 https://pubmed.ncbi.nlm.nih.gov/17823296/
o	Klossner et al 2007 https://pubmed.ncbi.nlm.nih.gov/17701424/
o	McKay et al 2008 https://pubmed.ncbi.nlm.nih.gov/18818249/
o	Deldicque et al 2008 https://pubmed.ncbi.nlm.nih.gov/18048590/
o	Murton et al 2014 https://pubmed.ncbi.nlm.nih.gov/24265280/
o	Jensen et al 2015 https://pubmed.ncbi.nlm.nih.gov/25677542/
o	Gidlund et al 2015 https://pubmed.ncbi.nlm.nih.gov/26089547/
o	Ogborn et al  2015 https://pubmed.ncbi.nlm.nih.gov/25695287/
o	Annabilini et al 2019 https://pubmed.ncbi.nlm.nih.gov/31143128/
My point is not made to speak against the value of your work, but I would suggest reframing the introduction to acknowledge there have been many studies of this nature and this is yet another but has a slightly different focus. One of the benefits of PeerJ is that the novelty is not a consideration here. Depending on your view of these references, a change to line 366 may be warranted.
•	Line 369: “We found that the changes in gene expression were highly dependent on the biopsy timing”. I would say that you need to say “We found that the conclusions/assertions/interpretations about the changes in gene expression…”. Just check for instances like this throughout but generally my sense is that you have may this qualification most of the time.
•	Line 387-390: Excellent, this is the central issue in the manuscript and in the field so I suggest making much more of this point in the Introduction and Discussion. Erroneous interpretations plague the field.
•	Line 396: proposed by whom? If so, why not measure it here? Overall I found this section and the IEG narrative to not work. I think it is very worthwhile to discuss the PGC-1 data but not as the current narrative. On line 411, the implication seems to be that the IEGs must be translated before changes in other mRNAs take place and that this is all very sequential. I find that hard to believe. A better explanation is that (as you describe later), the half lives of regulation of specific genes (independent of the IEG response) probably explains the gene-specific time courses. My read of your Discussion is that there is a lot of over-interpretation of what a change in mRNA means because it reads as though you are proposing that a change in mRNA of gene A indicates the role the function of the that gene’s protein A will have on gene B. That is simply not the case. So lines 391-453 need some work in my opinion as it ends up focussing too much on gene regulation of different genes (for which you do not have data on regulatory elements) rather than the interpretation of the data you have to hand in the context of your overall aims.
Experimental design: •	Overall the methods are described in nice detail, and experimental design has a lot of strong control/standardisation including the dietary control and the timing of later biopsies being devoid of influence of morning nutrition and circadian variation. In my opinion, the design with the baseline being 4 weeks before the HIIE is a major weakness, although you have done as good a job as you can in justifying it and cross-checking expression data in the straining study you reference. However, whatever about the basal expression of mRNA, the HIIE is performed by a muscle that is fundamentally different to baseline and given the effect of a training intervention on the acute molecular response to exercise, I think this point should at least be acknowledged in the Discussion. e.g. the lack of acute change or modest change in some genes may be a training effect. For example, the lack of change in GLUT4 (if I am interpreting the data correctly) could be explained by this point.
•	Related to this point, on line 125 you refer to the baseline biopsy timing being in order to reduce damage/stress but this seems to be a moot point given that there are then multiple biopsies in close temporal proximity and only 1 cm apart (which in my mind is unconventionally close together)?
•	Could you add a statement about the time that the HIIE took place after the most recent HIIE session?
•	Line 159: a sentence or two to explain the calculation of Wpeak is more preferable than the current statement.
•	I suggest that adding a horizontal dotted line a y=1 to indicate baseline expression would be a useful addition to all graphs.
•	It might help the reader to also have the graphs in Figs 2 and 3 organised in terms of regulators as one cluster e.g. top half, and the mitochondrial and metabolic markers as another cluster e.g. bottom half. At present, I don’t see a pattern to the way that the graphs have been organised. Just a tentative suggestion.
Validity of the findings: •	My major concern is the statistical analysis and given much of the rest of the manuscript hinges on these findings, I would expect that there may be major revisions of this submission depending on the outcomes of my concerns.
o	Have the data been tested for normality in order to proceed with t-tests?
o	What is the justification for using a 10%FDR rather than 5% which would be more consistent with the widespread use of p<0.05. Based on the q-values stated in Table 2, at an FDR of 5%, only 5 genes would have a peak that is statistically significant. I presume that the using the BH correction is in anticipation that the something like a Bonferroni is to stringent? Thus in both instances, you are increasing the chances of a Type I error. Of course this can be acceptable as an approach but in my opinion needs to be justified (small sample size, noisy data set, exploratory analysis, etc) with appropriate scientific references.
o	That said, given the research design and the stated aims, in my opinion a one-way ANOVA on the raw data (not fold change) with Dunnett’s post-hoc correction versus baseline is the appropriate statistical test.
•	The major issue with all of the above is that you are arguing throughout the submission that the timing of biopsy central to interpretation of the response to acute exercise, yet one could also argue that the statistical approach is also a major factor.
•	In Table 2, I would then ask the question is there such a thing as time to peak and magnitude of peak if there is not really a statistically significant peak in expression? This is particularly relevant to line 301-304, which are discussing changes where there are some gene with no changes evident based on the statistical analysis; and whether the data in Fig 4 and 5 can be considered valid if there were not statistically significant peaks?
•	Given the stated aim is around time course and how that affects interpretation, I find it conspicuous that you then ignore something like NRF-1 at 24 h given its statistical significance and especially given NRF-1 is a mitochondrial regulator, which you state is your interest (GLUT4 is not mitochondrial for example). Similarly if I am interpreting the data correctly, you have a major downregulation of CD36, so would it not be of interest to discuss a downregulated gene give the premise of the submission about the importance of interpretation?
Additional comments: •	Line 62 – Egan 2016 is not an appropriate reference here. Egan 2013 PLoS ONE perhaps?
•	Fig. 2 legend: Typo in title after GLUT4? And “except 6 participants”, there is no mention of the other time points being n=9.
•	I question the value of the 72 h data given (i) the n-size of 6 at 72 h, (ii) and the practical relevance of gene expression change at 72 h post-exercise considering that in both health and performance domains, the next training session will have almost certainly have taken place before this time.


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: INTERPRETATION OF EXERCISE-INDUCED CHANGES IN HUMAN SKELETAL MUSCLE MRNA EXPRESSION DEPENDS ON THE TIMING OF THE POST-EXERCISE BIOPSIES
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is well written and very clear. The authors clearly state the purpose of the work and why the study is relevant with the current gap in knowledge surrounding changes in mRNA expression following endurance type exercise over an extended 'acute' time course. Although a lot of literature exists surrounding acute mRNA responses to exercise the authors have well referenced relevant literature. The discussion although well written  is largely focused on PGC1-a, especially the first half, I believe it can be shorter and more concise.
Experimental design: Ln 112 – Is the reported VO2 peak value from baseline or following the HIIT intervention?
Ln 117 – Please confirm how many days the familiarisation trial was completed prior to the experimental trial for the collection of the ‘pre’ sample
Ln 119-121 – Please confirm how many days after the GXT the ‘pre’ biopsy would have been taken

Although the research question is well defined I do have several concerns regarding the design and timing of muscle sampling. Can the authors please address the following:

The timing of the ‘pre’ biopsy, 4 weeks prior to the acute post-exercise biopsies is a concern. For example the work by Miyamoto-Mikami et al. 2018, which the authors reference, did show that PPARGC1A (PGC1a) expression was up-regulated after 4 wks of HIIT, other groups have also demonstrated this (PMID: 23285255, PMID: 27604398). Other mitochondrial-related genes (PMID: 23285255), GLUT-4 (PMID 20010125) may be affected by relatively short training programs.
Although the purpose of the current study is to better describe the acute affect of exercise on gene expression an increase in basal expression of gene expression following training (i.e. if the ‘pre’ biopsy was taken after the training intervention) may not affect the interpretation of results. I do think the authors should acknowledge this as a limitation.

As the muscle biopsies following HIIE were completed in a trained state (following 4 weeks of HIIT) the authors should emphasize that the time points identified which correspond to the greatest increases in gene expression are in trained individuals. Training can alter the response to acute exercise bouts and therefore the timing in which the greatest increase was observed in these individuals may not be the same in untrained individuals.

Can you clarify how you identified the time point that elicited ‘the most extreme mRNA content of each gene’ was it simply the greatest numerical fold change? Other than the time points presented in table 2  were other time points also significantly different from pre? A few are mentioned in the text but if there are others this should be included in the table also and if this isn’t the case it can be stated that changes were only evident at the time point presented in the table.

Ln 264 -  Can you please clarify how basal mRNA content was calculated?

Ln 355 – as the authors state a clear relationship isn’t observed between mRNA expression level at baseline and the biopsy time point that had the biggest change in gene expression, this is clear in figure 5. But can you confirm how the lack of a relationship was determined? Was a correlation run? Why are only 5 genes highlighted in the figure 5?
Validity of the findings: The authors aimed to address a gap in knowledge with respect to temporal responses in gene expression following a bout of exercise. As mentioned above I think it is important to highlight that these results are in trained individuals (completed 4 wks of HIIT) and the increases reported may not occur at the same time point in untrained individuals.

The authors use a relatively small number of participants n=9 and n=6 at 72h, is this small sample size sufficient to detect differences in gene expression from baseline especially based on the large variability in responses?

Can the results described be extended to other types of exercise, specifically different modes of endurance exercise? This could be better reflected in the conclusion highlighting for the reader that different types of acute exercises may result in increased gene expression at different time points.
Additional comments: This is likely an oversight, however can you please confirm that the raw C(q) scores that have been submitted are actually the mean of the replicates?


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: INTERPRETATION OF EXERCISE-INDUCED CHANGES IN HUMAN SKELETAL MUSCLE MRNA EXPRESSION DEPENDS ON THE TIMING OF THE POST-EXERCISE BIOPSIES
Review round: 2
Reviewer: 1

Output:
Basic reporting: Nothing further to add from the first round of review.
Experimental design: Nothing further to add from the first round of review.
Validity of the findings: Nothing further to add from the first round of review.
Additional comments: Thanks for your revisions and your efforts to take my suggestions onboard as well as addressing my main concerns. I do have much more confidence in the results given the robust update to the analysis and therefore the manuscript is much improved. I only have very minor comments/typos that remain that you can take or leave as you wish:

- It may be worth removing Annibalini et al. 2019 despite my suggestion to include it as the timecourse there is a mix of muscle and blood, for your point about the timecouse of change in muscle, there are only two data points so it probably doesn’t support the point. That was my mistake to include that in the list.

- Throughout the manuscript, the terms mRNA content and mRNA expression are used (mRNA level/ expression level is also used in some places) - is there a specific reason why one is used in one instance and not in another? If not, it may be better to be consistent with one or the other?

- The phrase “most extreme mRNA” does not sit well with me. I know this is a change from the previous version but I am not sure it improves things. Would something like most changed/greatest change/peak/nadir etc work better?

- Line 364 - "exam" should be examining I think.

- Line 653 - “when the expression of downstream those genes targeted by PGC-1α was targets were examined” does not make sense to me and may need refining.

- Lines 695-699 - could the differences between exercise challenges have a role to play here? Even if not, it may be useful to add some description to what was used in each study.


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

Input:
Title: INTERPRETATION OF EXERCISE-INDUCED CHANGES IN HUMAN SKELETAL MUSCLE MRNA EXPRESSION DEPENDS ON THE TIMING OF THE POST-EXERCISE BIOPSIES
Review round: 2
Reviewer: 2

Output:
Basic reporting: The majority of my comments/concerns have been addressed. The introduction and discussion are improved and reference a greater number of previous studies to better describe the current state of knowledge in the field.

For clarity can you please describe the difference between figures 3 and 4? Do both figures use regression analysis to demonstrate the predicted peak in mRNA expression between 0-48h post HIIE? If this is the case there is no need to replicate the results in both figures (PGC-1a, PGC-1a4, PPARa, p53, PDK4, NRF1).
Experimental design: Thank you for addressing all my initial comments related to methods.
However, with the inclusion of new statistical tests can you please clarify your approach?
Did you use the Mann-Whitney U test to produce the p-value to enter into the Xiao “fusion scheme”? I do appreciate that an FDR adjustment was used on the Xiao values. I am a bit confused as to why the one-way ANOVA was performed, could you not run an ANOVA first (rather than the Mann-Whitney) then use the posteriori Xiao fusion scheme as a posthoc analysis?
Validity of the findings: Ln 406: Gene expression timing plotted against basal expression level
Can you be clearer on the relevance of this analysis? I appreciate the correlation shows no relationship between basal levels of gene expression and time of ‘peak’ expression but I don’t think the physiological relevance is well discussed.
Would evaluation of each gene individually not be more valuable? For example, are basal levels of a gene of interest (i.e. PGC1-a) related to time of increase in each participant? Especially if the authors state “For many genes, there was considerable individual variability for the time-point at which the most extreme mRNA content was observed, especially for genes that responded at later time-points.” (ln 424-426)
Additional comments: As a general comment when discussing previous work describing the impact of exercise on gene expression I think it would be useful to include some information surrounding the intervention used. Occasionally this information is included but not always for example Ln 514-516 Hammond et al 2016 was following a steady state bout of exercise (which was preceded by a HIIT session several hours earlier) whereas Edgett et al 2013 used a bout of HIIE.
Ln 301: when examining
Ln 548-549: consider revising for clarity
Ln 552: “Based on this model, we mapped out the time window eliciting the highest or lowest 10% of gene expression after exercise (Fig. 3).” is this not Figure 4?


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: INTERPRETATION OF EXERCISE-INDUCED CHANGES IN HUMAN SKELETAL MUSCLE MRNA EXPRESSION DEPENDS ON THE TIMING OF THE POST-EXERCISE BIOPSIES
Review round: 3
Reviewer: 1

Output:
Basic reporting: No further comments.
Experimental design: No further comments.
Validity of the findings: No further comments.
Additional comments: Congratulations on a nice piece of work.


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

Input:
Title: INTERPRETATION OF EXERCISE-INDUCED CHANGES IN HUMAN SKELETAL MUSCLE MRNA EXPRESSION DEPENDS ON THE TIMING OF THE POST-EXERCISE BIOPSIES
Review round: 3
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Thank you for addressing all my revisions I don't have any further comments.


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

Input:
Title: BAYESIAN COMPUTATION FOR THE COMMON COEFFICIENT OF VARIATION OF DELTA-LOGNORMAL DISTRIBUTIONS WITH APPLICATION TO COMMON RAINFALL DISPERSION IN THAILAND
Review round: 1
Reviewer: 1

Output:
Basic reporting: Minor. Lines 15, 43, etc., describe rainfall as following a delta lognormal distribution. The authors consider daily rainfall. Add “daily” throughout (e.g., replacement at line 81).
Experimental design: No comment
Validity of the findings: My sole major concern is that the authors’ Monte-Carlo simulations were made for the delta log-normal. The authors find good performance with the equal-tailed Bayesian based on the independent Jeffreys prior (Figures 1-4). For that analysis type, please add additional simulation with small discrepancy to the probability distribution and evaluate coverage under such conditions.
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: BAYESIAN COMPUTATION FOR THE COMMON COEFFICIENT OF VARIATION OF DELTA-LOGNORMAL DISTRIBUTIONS WITH APPLICATION TO COMMON RAINFALL DISPERSION IN THAILAND
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper investigates the estimations for the common coefficient of variation of delta-lognormal distributions. The Bayesian parametric estimators are derived. They compare the new estimator with three existing estimators by using simulations and real data(rainfall data in Thailand) analysis. The results show that the equal-tailed Bayesian based on the independent Jeffreys prior was suitable.
It is interesting to give the Bayesian confidence intervals for the common coefficient of variation of delta-lognormal distributions. The results are reasonable and correct.
Experimental design: no comment
Validity of the findings: The emphasis of this article is not confirmed,It should be an applied one, just from the title.In this case,It should start with the actual issue(rainfall data) to illustrate the importance of interval estimation.From the existing literature,the rainfall data follow the delta-lognormal distribution,while, the existing confirm interval estimates are not available based on this data,it necessary to study the estimation based on the Lognormal distribution.Then,the next issue is the difficulty of direct estimation?The reason to take Bayes? At last,conclusion with estimate data from simulation & data. The reasonable illustrate of the research methodologies is not available,just copy & paste.
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: BAYESIAN COMPUTATION FOR THE COMMON COEFFICIENT OF VARIATION OF DELTA-LOGNORMAL DISTRIBUTIONS WITH APPLICATION TO COMMON RAINFALL DISPERSION IN THAILAND
Review round: 1
Reviewer: 3

Output:
Basic reporting: The paper is interesting. However, the motivation should be given for more details and discussion section must be provided.
Experimental design: See the attached file
Validity of the findings: The methods used in this work is quite similar to the paper of the authors published in PeerJ in 2019. This work uses population group k > 2.
Additional comments: Please see the attached file


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: BAYESIAN COMPUTATION FOR THE COMMON COEFFICIENT OF VARIATION OF DELTA-LOGNORMAL DISTRIBUTIONS WITH APPLICATION TO COMMON RAINFALL DISPERSION IN THAILAND
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: In my previous review, I wrote: My sole major concern is that the authors’ Monte-Carlo simulations were made for the delta log-normal. The authors find good performance with the equal-tailed Bayesian based on the independent Jeffreys prior (Figures 1-4). For that analysis type, please add additional simulation with small discrepancy to the probability distribution and evaluate coverage under such conditions.

The authors added sigma^2 = 0.1 to Table 1 and Table 2. This was the addition of small variances. That is not what I requested. The problem is that the authors assumed delta log-normal and then did simulations with delta log-normal. Figure 2 are important but not persuasive. To simulate "discrepancy to the probability distribution" please generate delta log-normal as currently, and then add additional noise additive (mean 0) or multiplicative (mean 1), as the authors think best, and assure that the coverage performance shown in Tables 1 and 2 do not deteriorate substantially.
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: BAYESIAN COMPUTATION FOR THE COMMON COEFFICIENT OF VARIATION OF DELTA-LOGNORMAL DISTRIBUTIONS WITH APPLICATION TO COMMON RAINFALL DISPERSION IN THAILAND
Review round: 2
Reviewer: 2

Output:
Basic reporting: All my concerns are corrected.
Experimental design: -
Validity of the findings: -
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: TESTOSTERONE AND ESTRADIOL AFFECT ADOLESCENT REINFORCEMENT LEARNING
Review round: 1
Reviewer: 1

Output:
Basic reporting: Thank you for considering me as reviewer for PeerJ.

Professional English language:
The authors’ language is clear and understandable (although it sounds rather like German). However, the English language is not as professional as I would expect it to be in a scientific manuscript. Tenses are not always used correctly (e.g. future tense in line 56 f.; line 389: “we could confirm”-> we confirmed), sentences are rather long, and, in general, the language sounds colloquial (e.g. line 242). I suggest you have a colleague who is proficient in English and familiar with the subject matter review your manuscript. (I am no native speaker either)

Intro & Background:
After I have read the title and abstract, I expect to read a manuscript about hormonal influences on adolescent reinforcement learning behavior. The Introduction however, describes the neurobiological background of reward learning very profoundly. I understand that you need to describe the background of the dopaminergic reward system a little bit, but I think you go into this too deeply. I recommend to focus more on studies describing hormonal effects on reward processing in general, with emphasis on behavioral work in humans. I know that there is not much literature about this topic, but here you could stress why your work is a real contribution to the field.
And also, if you did not measure DA and 5-HT, do not put too much emphasis on it in the first place. I would be careful with simply stating that your task can be used as a proxy for DA and 5-HT.

Structure conforms to PeerJ standards and discipline norm. -> yes

Figures are relevant, well labelled and described. The figure legends in Figure 2 and 3 are very small.

Raw data supplied -> yes
Experimental design: Original primary research within scope of the journal -> yes

The research question is interesting and meaningful for understanding the development of certain behaviors and, on a more general level, typical mental disorders in adolescents (depression, substance use disorder, ADHD etc.). However, that’s what I would like to read a little bit more in Introduction and Discussion. The interesting part of your study is how you’ve tried to understand a possible effect of sex hormones on reward learning during pubertal age – because you can assume that hormones critically affect behavior during puberty.

Rigorous investigation performed to a high technical & ethical standard. -> yes

Methods described with sufficient detail and information to replicate. -> yes
Validity of the findings: All underlying data have been provided; they are robust, statistically sound, and controlled. -> yes. Data analysis and results are reported sufficiently. The analysis methods are chosen correctly to answer the research questions. Effect sizes are reported.

Discussion and Conclusions:
See my comments on the Introduction. I advise against describing to many neurobiological details. Especially lines 346-358 and lines 406-419 could be densed and rewritten for readers with less neurobiological background, i.e. a broader audience.
Additional comments: -	Did you check for the onset of menses in girls? If they already had their menses, in which menstrual cycle phase did you measure? This could have a major impact on interpreting your results (see also Diekhof 2015).
-	What do you mean with “optimal hormonal concentrations” (line 152)? Is there an optimal hormonal level? Please describe.
-	I recommend not using too many abbreviations. It hinders the reading flow. At least, I would fully spell out testosterone and estradiol. But that is a rather personal opinion.


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

Input:
Title: TESTOSTERONE AND ESTRADIOL AFFECT ADOLESCENT REINFORCEMENT LEARNING
Review round: 1
Reviewer: 2

Output:
Basic reporting: Basic reporting:
1.	English language should be improved throughout to ensure that ideas are clearly communicated. Current examples of awkward phrasing include line 30, 39-40, 42-44, 123-125, 126-129, 133-135 and several others. Current phrasing makes comprehension difficult.
2.	Line 32- Units of age should be specified (years).
3.	Introduction
a.	Primary issue:
i.	The structure of the introduction is not intuitive. Why does it start with such a specific focus on dopamine when neurotransmitter levels are not even measured in this study? It would seem to make more sense to focus on the context of the results presented. For example, it sounds like the take away message is that sex hormones have common and dissociable sex-dependent effects on different aspects of reinforcement learning. Therefore, it would seem that an introduction covering sex differences in cognition during adolescence and the moderating effects of estradiol and testosterone would be more helpful in orienting the reader. Such an extensive discussion of dopamine and serotonin would be more appropriate for the discussion.
b.	Other comments on the introduction:
i.	In the paragraph on steroid hormone interactions with dopamine and serotonin, there is no mention of the extensive literature from human subjects that provide additional translational support for such interactions.
ii.	The statement at line 112 is inaccurate. The authors state, “In adolescents, a rising hormonal level contributes to pubertal development, whereas in adults a constant sex hormone level maintains reproductive function.” However, adult women do not have constant hormone levels. Also, maintaining constant estrogen/progesterone levels would suppress ovulation.
iii.	The citation at line 126 should be “Jacobs & D’Esposito, 2011” not “Cools & D’Esposito, 2011”
4.	The structure of the discussion is similarly confusing and circuitous.
Experimental design: Experimental design:
1.	Was menstrual cycle phase accounted for? This also would affect DA and 5-HT
2.	Why were RTs under 200 ms discarded? How many data points was this? Was this throughout blocks or just the first trial?
3.	Age should be included as a covariate in the primary statistical model evaluating sex. Age effects should also be controlled for when examining pubertal effects, either by including it as a covariate if not co-linear or by first regressing age effects and performing further analyses on residuals. Although there is no significant difference in age between male and female groups (though arguably, age should still be controlled for in this case given that this is a developmental sample), the authors also examine other factors such as hormones and pubertal effects. Not controlling for age in a developmental sample is a fundamental flaw.
4.	The authors interchangeably use terms for sex and gender. Terms should be consistent. If sex was studied, terms should be sex, male, and female. If gender was studied, terms should be gender, boys, and girls.
5.	Given the current use of language, it is unclear if the methods are described in sufficient detail to replicate.
Validity of the findings: Validity of Findings
1.	Data have not been provided in a repository.
2.	The paragraph under “conclusion” seems only tangentially related to actual results. It would be helpful to have a sentence that clearly links results to conclusions to ground readers.
Additional comments: In this manuscript, Kohne and Diekof examine correlations between endogenous hormones and reinforcement learning in male and female adolescents. They found associations between markers of reinforcement learning and levels of estradiol and testosterone. While this is an important topic, and literature regarding hormone and pubertal effects on cognitive development are essential to furthering our understanding of normal and abnormal brain development, my enthusiasm is diminished by the structure of the manuscript and awkward use of English.


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: TESTOSTERONE AND ESTRADIOL AFFECT ADOLESCENT REINFORCEMENT LEARNING
Review round: 2
Reviewer: 1

Output:
Basic reporting: The English language has much improved and sounds professional now.

Intro & Background:
My comments regarding Introduction and Background have been adressed sufficiently. The reader can follow the thoughts of the authors and is able to understand the rationale of the study.

Structure conforms to PeerJ standards and discipline norm. -> yes

The figures are very small in the PDF file. I hope this is just a copy and paste issue and will be restored during production?

Raw data supplied -> yes
Experimental design: Original primary research within scope of the journal -> yes

Research question well defined, relevant and meaningful. It is stated how the research fills an identified knowledge gap. -> yes, all my comments have been adressed.

Rigorous investigation performed to a high technical & ethical standard. -> yes

Methods described with sufficient detail and information to replicate. -> yes
Validity of the findings: all my comments have been adressed.
Additional comments: all my comments have been adressed.


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: TESTOSTERONE AND ESTRADIOL AFFECT ADOLESCENT REINFORCEMENT LEARNING
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors present a valuable study on understanding the effect of testosterone and estradiol on adolescent reinforcement learning. Data are well presented, however, authors need to amend a few parts of the English language. Confusion in understanding the context can be observed in certain part of paragraphs.
Experimental design: Please refer to the main article.
Validity of the findings: Please refer to the main article.
Additional comments: No additional comments