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: UNCOVERING THE HIDDEN DIVERSITY OF MISSISSIPPIAN CRINOIDS (CRINOIDEA, ECHINODERMATA) FROM POLAND
Review round: 1
Reviewer: 2

Output:
Basic reporting: This is a well-written and well-referenced contribution, with proper attention paid to previous studies of regional crinoid faunas.  The structure of the manuscript is logical, in keeping with established conventions for systematic descriptions.  I commend the protocols for keeping certain taxa in open nomenclature rather than omitting their descriptions entirely or assigning them to an overly speculative taxonomic identity.  All relevant raw data, including museum specimen numbers and measurements, are clearly provided, as are justifications for identifications (or lack thereof) of incomplete material.

Areas where some revision is warranted include the following:

1. Figure 1 and associated captions are unclear.  It should be made clear that panel A is an overview map of Poland with the regions depicted in the other panels denoted by corresponding letters.  Or, even more effectively, the outlines of the geologic regions shown in panels B-D should be included in the map of Poland in panel A.  Also, in keeping with journal formatting, the dates for the references in the captions should be in parentheses.

2. In the "Stratigraphical setting" section, the number of specimens collected from each site should be mentioned.  This will allow readers to more fully link the geologic setting to the detailed specimen descriptions provided later in the manuscript.  Nearly ALL of the material described in this manuscript (10,000+ specimens) come from the Holy Cross Mountains, with only a single specimen described from the Debnik Anticline and only a single specimen described from the Upper Silesian Coal Basin.  This distribution of material should be made clear in the beginning of the paper.

3. On line 86, it is stated that crinoids had been previously reported from the Mazurowe Doly Formation.  The nature of that crinoid material should be made clear (i.e., isolated crinoid columnals vs. articulated material; taxonomically identifiable vs. unidentifiable material).

4. Should the descriptions for Cladida indeterminate A and Cladida indeterminate B moved to an earlier position in the systematic section?  It seems logical that they would immediately follow Parvclass Cladida on line 273.
Experimental design: The methods employed are very clear and thoroughly explained, and the findings presented in this study are appropriate for publication in this journal.  The research question is stated clearly, and the novel data fill a gap in the existing knowledge of Polish crinoid faunas.  Methods are described in sufficient detail to permit replication.

Areas where some revision is warranted include the following:

1. On line 167, please use only mm for describing the size of mesh.  If the symbol before "1.0" is supposed to be phi, then this is an incorrect symbol.

2. On lines 170-171, it is stated that 19 polished slabs were prepared for examination, but are not described, figured, or discussed further in this report.  What is the significance of these polished sections---do they contain any relevant data?
Validity of the findings: The data presented in this study are well-supported and fit with the most up-to-date knowledge of crinoid morphology and taxonomy.  Conclusions are linked to detailed descriptions and figured specimens.

Areas where some revision is warranted include the following:

1. The high morphological disparity of brachial plates is used as evidence of high biodiversity on lines 526-527; however, the fact that columnal morphology varies along a column is stated on line 540.  Brachial morphology also varies along crinoid arms.  Are you stating that morphological diversity is a reflection of biological diversity for brachials but not for columnals?

2. This is not a criticism, nor is it a required change, but I am curious about the abundance of columnal/pluricolumnal material relative to brachial material.  I've worked with several deposits--both carbonate and siliciclastic--that are dominated by isolated ossicles, but with far greater numbers of brachials compared to columnals.  Other crinoid researchers have also asserted that brachials are typically the dominant crinoid bioclast, but that this pattern is poorly documented.  Anything that you can add to this manuscript addressing this pattern, whether it be an issue of perception or a genuine bias in the crinoid fossil record, would be very welcome to those of us who work extensively with disarticulated crinoid material
Additional comments: I commend the authors on this detailed, well-written, and well-illustrated study.  Research focusing on "ugly" crinoidal material, including isolated ossicles and fragmentary specimens, is quite important given the echinoderm fossil record and can provide significant insights into depositional processes, paleobiogeographic distributions, paleoecology, and taphonomy.  However, this material is far too often ignored or given hasty treatment.  Studies such as this should be strongly encouraged, as easily overlooked specimens can generate valuable information on echinoderm diversity (taxonomic and/or morphologic) and occurrence.

Please feel free to contact me if you have questions or if there is anything that I can provide greater clarity on.  Thank you,

James R. Thomka*

Center for Earth and Environmental Science
State University of New York at Plattsburgh
Plattsburgh, New York 12901, USA

*jthom059@plattsburgh.edu


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

Input:
Title: COMPARATIVE PHOSPHOPROTEOME ANALYSIS TO IDENTIFY CANDIDATE PHOSPHOPROTEINS INVOLVED IN BLUE LIGHT-INDUCED BROWN FILM FORMATION IN LENTINULA EDODES
Review round: 1
Reviewer: 1

Output:
Basic reporting: Song et al. performed phosphoproteome analysis in L. edodes. This manuscript lacks many important descriptions, which may cause misunderstanding. Also, I could not find any importance in fungal biology. So, I do not recommend to publish this manuscript.

Specific comments
1.	No importance in phosphoproteome is stated in the current manuscript, although I also suppose it may be important. Why was comparative/differential phosphoproteome analysis conducted in the two samples? Especially, relationship between blue light and protein phosphorylation was not described. Just performing experiment and analysis using new samples?

2.	The authors state that many DPPs were identified. But, I suppose most of them may be proteins differentially expressed between the two samples, but not those of which phosphorylation levels differ. Did the author analyze simple proteome analysis using total proteins from the two samples to normalize? I could not find any descriptions about this in the current manuscript. If not, the manuscript should be rewritten to avoid misunderstanding.

3.	The culture condition is not well described. What medium was used in this study? What is the sources of blue and red light? Was the incubator illuminated all day or under cycles such as 12 h ON/ 12 h OFF?

4.	Discussion must be rewritten because it does not contain “discussion” based on the results, but many descriptions that could be used for Introduction of the other manuscripts. Almost of the descriptions are not relate to this study and the results. The most serious description is lines 351-354, which is not new finding in this manuscript.

5.	I suppose many proteins that exhibit affinity to metal ion are listed, suggesting enrichment of phosphorylated proteins by IMAC may not be enough or background is high.

6.	Lines 232-243: Is this description based on the MS analysis or genome database?
Experimental design: The authors state that many DPPs were identified. But, I suppose most of them may be proteins differentially expressed between the two samples, but not those of which phosphorylation levels differ. Did the author analyze simple proteome analysis using total proteins from the two samples to normalize? I could not find any descriptions about this in the current manuscript. If not, the manuscript should be rewritten to avoid misunderstanding.
I suppose many proteins that exhibit affinity to metal ion are listed, suggesting enrichment of phosphorylated proteins by IMAC may not be enough or background is high.
Validity of the findings: I suppose phosphoproteome itself is important.
Additional comments: No additional comments


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

Input:
Title: COMPARATIVE PHOSPHOPROTEOME ANALYSIS TO IDENTIFY CANDIDATE PHOSPHOPROTEINS INVOLVED IN BLUE LIGHT-INDUCED BROWN FILM FORMATION IN LENTINULA EDODES
Review round: 1
Reviewer: 2

Output:
Basic reporting: Song and coworkers have applied a phosphoproteomic approach to identify phosphorylated proteins whose formation is influenced by blue light. The experimental methods used for this purpose seem to have been applied with experience and care. I have, however, several concerns about the bioinformatic approach used to identify the respective phosphoproteins:
Experimental design: As for the "biological" experiments, I have no concerns. They are brief and simple, and the techniques described clearly.
Validity of the findings: As noted above, there are several problems:

1.	 The resulting MS/MS data were processed using the Maxquant search engine (v.1.5.2.8), and queried against a human Uniprot database concatenated with a reverse decoy database. This is a standard procedure in most studies. However, protein sequences of Human orthologs that can be found in Lentinus edodes are usually poorly conserved, and one would have to be very lucky to find peptides that bear the similarity that the authors claim. The genome of Lentinus edodes has been sequenced (Chen et al. PLoS One. 2016;11(8):e0160336) and it would therefore be possible to retrieve the sequences for the whole putative proteins of all the identified peptides. This would put the putative identification of the phosphopeptides on a much more reliable level. A (supplementary) table that lists these peptides, the respective proteins deduced from the genome sequence, and their accession numbers needs to be presented.

2.	I have a similar problem with GO and KEGG analysis: GO is very popular because it enables an enrichment analysis of proteins belonging to the same category. However, GO has not been optimized for multicellular fungi, but is strongly based on yeast, plant and bacterial databases. Consequently, GO analysis always introduces an identification error of 5-10 % with fungal proteins, and I am afraid that this would be particularly the case if only peptides are used. This problem could be solved in a similar way as above: don’t use the peptides but the full length proteins (extracted from the genome sequence), and compare the resulting identity with the results of a blast search and conserved domain analysis. Such a (supplementary) table, including the best hit and its statistics, needs to be presented.

3.	As for the KEGG analysis, I request that the authors name the proteins that they claim to be enriched rather than only giving the KEGG group, because some of the groups provide no information. Examples: “fructose metabolism”. Fructose can be metabolized by the glycolytic pathway without any additional enzyme, and I therefore wonder which protein gave rise to this claim of enrichment. Or “galactose metabolism”: I looked up the respective KEGG pathway sheet and found that it lacks the enzymes of the alternative, reducing galactose catabolic pathway that has been identified in fungi. So do the authors mean the Leloir enzymes? I believe this attribution of phosphoproteins to KEGG groups needs to be included in the Supplementary Table I requested above.
I believe these the above three points are essential to present the results of this study in a way that it provides a useful and reliable information to the readers. Yet there are additional points that should be considered too:
Additional comments: The authors detect phosphorylation in glycoside hydrolases and their polysaccharide binding domains. This is new. Phoshorylation has been detected in the carbohydrates of the attached glycan chains of these glycoproteins but never on the proteins themselves. The authors should discuss the potential significance of this finding. Phosphorylation of a protein alters its isoelectric point and consequently the solubility. Would the phosphorylation improve solubility or binding to the substrate? This is a point where a rather simple experiment could have contributed significantly to the paper.

One limitation of the paper is its descriptive nature, and the use of broad categorizations in the present manuscript does not allow any clear insights. It would significantly improve the manuscript if the authors would be able to provide some additional experiments that prove the importance of some of the identified peptides in the response to blue light.

In Table1 (List of differentially expressed signalling proteins) the authors use a cut-off of 1.5-fold. This appears very low to me. In transcriptome analyses, a log2 >2 is the current


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

Input:
Title: COMPARATIVE PHOSPHOPROTEOME ANALYSIS TO IDENTIFY CANDIDATE PHOSPHOPROTEINS INVOLVED IN BLUE LIGHT-INDUCED BROWN FILM FORMATION IN LENTINULA EDODES
Review round: 1
Reviewer: 3

Output:
Basic reporting: Overall there is comprehensive information provided, but still clarity is lacking in few aspects.
Some figures are mislabeled, and also resolution for figures is poor. A couple of them are hard to see/read (details below). In the introduction, authors very briefly touch through the blue light photoreceptors. However, in the context of this manuscript it will be nice to have some more background on their biological roles specifically in context of Lentinula edodes. Also, authors are missing some very recent important references such as Yoo Seung-il et al, BMC Genomics 20, 121 (2019) though on transcriptional study but is highly in context of this particular study. One another reference is Kim J Y et al, PLoS ONE 15(3): e0230680 (2020). These should be briefly discussed. Raw data is provided in the supplementary tables.  Language is mostly clear.
Experimental design: Experimental:
Information on experimental replicates is not clear. It seems three biological replicates are taken. Are they take in parallel, or on three different times? Authors should clarify this in text. Also, methodology section needs more clarification. Points mentioned under general comments.
Validity of the findings: No Comment
Additional comments: This is a novel study elucidating differential phosphoproteome involved in mycelial browning of basidiomycete fungi Lentinula edodes. Overall there is comprehensive information provided, but still clarity is lacking in few aspects. More expansion in introduction in needed to strengthen the foundation of study, and in discussion section to justify the key experimental inferences.

1.	A better picture with higher resolution will be good for the red vs blue light treatment of the L. edodes. (Fig 1A)
2.	Instead of just stating blue or red light, authors should also provide lumen intensity of the lights used in this study.
3.	In the material and method section, trypsinization strategy is confusing. Were there two rounds of trypsinization one after another (Lines 147-149).
4.	Which TMT kit?, What IMAC spheres were used Fe, Ti,..?? Provide more detailed and accurate description.
5.	Include more description on how the phosphosites were identified, and how is the quantification done.
6.	Figure 1C, hard to read the axis of the graph
7.	Figure 2B, Label axis
8.	Figure 3B is mislabeled in the legend, also not clear how is B different from A
9.	Figure 4C, provide more description on the intensity map (to clarify the understanding, distance and position are cleat, what does red and green signify in fig 4C, numbers or something else)
10.	Legend not accurate. 5C? Also, resolution of figures very poor, hence sometimes difficult to read no's
11.	Line 297, correct Fig7B to 7A
12.	Did authors see/analyze any change in localization of proteins in red vs blue light treatments? That will be an interesting information which can be easily fished from the given data.
13.	Authors, should expand the discussion section adding some key points. A. For DPP, KEGG enrichment analysis (Fig7) up-regulated phosphorylated proteins show ABC transporters, and ribosome biogenesis phosphorylated proteins. authors should put this in discussion, as why they think these are upregulated and possible relevance to brown film formation. B. Expanding on the similar lines, for top upregulated domains, ABC transporter like, P-type ATPase, etc.
Similarly, discussion should be expanded more for downregulated phosphorylated proteins and domains.


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

Input:
Title: COMPARATIVE PHOSPHOPROTEOME ANALYSIS TO IDENTIFY CANDIDATE PHOSPHOPROTEINS INVOLVED IN BLUE LIGHT-INDUCED BROWN FILM FORMATION IN LENTINULA EDODES
Review round: 2
Reviewer: 1

Output:
Basic reporting: The MS has been modified as I had required.
Experimental design: Non
Validity of the findings: Non
Additional comments: Non


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

Input:
Title: COMPARATIVE PHOSPHOPROTEOME ANALYSIS TO IDENTIFY CANDIDATE PHOSPHOPROTEINS INVOLVED IN BLUE LIGHT-INDUCED BROWN FILM FORMATION IN LENTINULA EDODES
Review round: 2
Reviewer: 2

Output:
Basic reporting: Manuscript is improved, and basic reporting is fine.
Experimental design: Explained better
Validity of the findings: Fine
Additional comments: Revised manuscript has addressed most of the concerns. Figures, seemed to be improved. I recommend accepting the article. Though text reading for minor text mistakes is needed.


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: USE OF NEXT GENERATION SEQUENCING TO COMPARE SIMPLE HABITAT AND SPECIES LEVEL DIFFERENCES IN THE GUT MICROBIOTA OF AN INVASIVE AND NATIVE FRESHWATER FISH SPECIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: The overall manuscript is written ok. The structure could be improved with a more in depth literature review as noted. Some incorrect uses of references. Please check references and perhaps add some additional ones focused specifically on fish microbiomes. For the last paragraph of the introduction, I would encourage having a couple of overview sentences describing the general sampling strategy to test your hypotheses. The figures and tables are ok. The author cites the github page in the abstract but the link shows that nothing is listed. This needs to be made publically available or at least available to reviewers during the review stage.
Experimental design: Primary research aim:
The primary research question was to what extent a new storage buffer enabled the preservation of the gut microbiome of the fish. The author claims the buffer can be used to store samples for 4-8 weeks without cold storage but does not actually test this. The main point of the article is that they've developed a method to enable collection and storage of gut microbiomes from the field.

Scope cont.: It would make for a more compelling manuscript to describe the extent of fish diversity which would benefit from this. In other words, of the 35000 fish species, how many of them are located in remote locations where sampling is perhaps even impossible. I realize it would be difficult to give absolute numbers here but it would be useful to consider describing this a little more in the introduction.

The authors decided to focus on the validation of the technique, but did not test this thus the investigation was not rigorous. The authors may perform this analysis and submit findings in a revision.
Validity of the findings: For microbiome analyses, the author omits alpha diversity from the comparisons between species and comparisons in habitat for the gobies. This should be performed and compared using a non-parametric pairwise comparison e.g. Mann-Whitney. This would likely reveal the bullhead fish having higher richness and within gobies likely no differences in richness when comparing the sites. For both figure 2 and figure 3, the author compares the species and habitats using NMDS. While this is a fine measure, I would suggest and encourage the authors to explore additional beta diversity comparison methods which take into account phylogenetic differences in the microbial community (e.g. Unifrac distances). At the very least, utilizing methods such as Jaccard and or Bray-Curtis would enable additional comparisons which might further support the observations made. Figures 4 and 5 could be combined into one figure with two panels. Its not appropriate to just pick the top 3 OTUs. Also note that compositionality makes it impossible to determine true biomass or even changes or differences in communities. For instance, its possible that Aeromonas is higher in gut samples from Eagle Wings compared to Governors Island, but its equally likely that there are simply more other types of taxa in Governor’s Island and Aeromonas is the same. To deal with this problem, one can use ranks or ratios.
See, https://doi.org/10.1016/j.annepidem.2016.03.003
Additional comments: Developing new collection methods is important and while you have shown that you can distinguish a species effect and habitat effect based on samples collected with your method, you do not actually verify or test the method itself. If the focus of the manuscript is to be on the method, you will have to perform experiments which justify the buffer use. This could include a time series of a few samples processed with different storage methods. You can then compare both alpha and beta diversity changes. Alternatively, the dataset in itself has relevant biological findings which could also be a main focus rather than the storage method. That being said, it would still be important to justify this storage method and confirm that the differences in community structure are not simply from a storage effect.


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: USE OF NEXT GENERATION SEQUENCING TO COMPARE SIMPLE HABITAT AND SPECIES LEVEL DIFFERENCES IN THE GUT MICROBIOTA OF AN INVASIVE AND NATIVE FRESHWATER FISH SPECIES
Review round: 1
Reviewer: 2

Output:
Basic reporting: Gallo et al investigated the gut microbiota of a native an invasive fish species collected from the St. Lawrence River using a 16S-amplicon sequencing approach. As the author emphasized in the introduction, investigation of the gut microbiota of fish is emerging in the filed of the Gut microbiome and it is necessary to understand microbial ecology of fish in the filed of the vertebrate gut microbiome. Although the data presented provided in this manuscript is quite simple, however, all the procedure from sampling to bioinformatic analysis follows the standard methodologies which I see as a strong point of the manuscript.

Only one point that needs to be clarified in the introduction and discussion is what the authors suggested from this study. If this manuscript aims to provide an overview of the gut microbiome composition and structure in two selected fish species (an exploratory study) the data that have been presented are relevant. However, from some part of the manuscript (i.e. line 79-82), it seems that authors suggesting the methodology used in this study as a standard SOP for all fish related gut microbiome analysis, which I believe is an oversimplification. Just as an example, although NAP buffer showed some promising results in one study for mammalian samples (Camacho 2013), it does not mean it provides the same good preservation picture for fish gut digesta. So, I believe unless you a clear comparison of the current state of art approach like snap frozen, RNALater, Omnigen buffer, Zymo storage buffer, etc, the conclusion that the author made in this manuscript is not robust enough. The same for DNA extraction.
Experimental design: As I explained partly in the Basic Reporting section, If we consider this manuscript as a preliminary exploratory analysis effort (and note a methodological suggestion paper), the experiments were done in a proper way. However, some improvements can be done.
 1. One important point to mention for this section is the low number of fish selected for this analysis. I believe this is one of the key limitations of the manuscript that should be mentioned in the discussion section( e.g why this sample size).
2. Another type of analysis that could have added more information and insight to this manuscript is to use the functional prediction tool on their 16S dataset to have also an overview of the functional profile of the fish gut microbial communities. I suggest that given to reliable bioinformatics tools that are available for this purpose, the authors follow up on that and add the relevant multivariate analysis and discussion, too.
Validity of the findings: Given the high interindividual variation in animals such as fish, choosing a proper sample size is a critical factor for the microbiome analysis. While the methodology used in this manuscript followed the state of art approaches, the small sample size selected in this study could be a problem for reproducing the same findings by another research.
Additional comments: In General, I believe this study was a nice effort to provide a preliminary overview of the gut microbiome in two native and invasive freshwater fish species in St. Lawrence River and to show how in general the gut microbial community affected by the different habitats. Although the study suffers from a small sample size, however, the overall methodology was according to current standards in the field of microbiome research. By adding the prediction of functional annotation and relevant analysis and discussion to the current manuscript, I believe the manuscript can be accepted for publication.


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

Input:
Title: USE OF NEXT GENERATION SEQUENCING TO COMPARE SIMPLE HABITAT AND SPECIES LEVEL DIFFERENCES IN THE GUT MICROBIOTA OF AN INVASIVE AND NATIVE FRESHWATER FISH SPECIES
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript is a well-written and useful summary of the current status of “data publication” from a certain perspective. The authors, however, need to be more analytical. This manuscript does an excellent job showing a new protocol that can be easily used to take fish gut samples in the field that can be used to gut microbiome analysis without using -80 oC to preserve the samples until further microbiome analysis. The paper would be both more compelling and useful to a broader audience if the authors provide a better picture of the factors that drove the gut microbial community in fish as well as the importance of the host’s physiology and health.

Related to the title, it is suggested to modify the title. NGS has been used widely in gut microbiota studies in fish, the main focused on the paper is the NAP buffer procedure used to eliminate the need for refrigeration of samples at -80oC. The title should be more tied to that.

In the introduction, there are some facts related to the factors that address the microbial community in the fish gut, as well as, the effect in the host physiology and health. A suggestion, all the paragraphs should be reorganized as there are some sentences that are very redundant. The statement of the factors leading the gut microbiome composition and colonizing needs more facts to support it.
Experimental design: The section material and method are very clear, however, along with the description there is some lack of information that requires description:
It is important to describe the sampling time and the season. In the case of environmental studies of the gut microbiome in fish, the season time has shown to have a very important effect on the feeding behavior of the animals. As well, if the animals were sampled at different days or different sampling times, they could have been affected by the digestion process as the animals in nature compared with cultured fish have their feed all time.

As well, to know the size of the animals caught would be very helpful in order to have an idea of the life stage of the animals studied which complements the fact of their different trophic feeding behavior.

The paragraph between line 189 to 191, the statement of the Atlantic salmon: This statement requires to be rephrased. The information is a little confusing. Inline 54, eliminating the word can. In the sampling procedure, did you consider sampling some water?
Validity of the findings: The discussion of data citation was good and captured the state of the art well, but again I would have liked to see more discussion on their findings.

In the discussion, the authors might consider some questions: 1)if the 2 euthanasia protocols used in the sampling time could affect the gut microbiome composition. It has been shown that the psychical stress caused by human handling can affect the gut microbiome in fish.
2) The possible effect due to washing and removal of the digestive feed on the DNA extraction as well need to be considered. It has been shown that this could cause some troubles in the bacterial DNA extraction in gut microbiome studies.

How could it be explained why the microbial composition in the governor’s islands is so disperse compared to the eagle wings? As well, why is it so abundant the presence of bacterial strains like Aeromonas and Clostridium that has been associated with fish disease?

The possible differences between Round Goby at different depths should consider the effect of the two different sample points besides the depth. It will be very interesting to study if the NAP buffer will give the same results in the same samples at 4 weeks or 8 weeks prior to DNA extraction.

Prior to reading the manuscript, I thought the results section of the paper was going to be promising and relevant, but it is somehow light information. It would be better if the richness and diversity identified were presented on a table with other diversity indexes like Shannon, Simpson, etc. As well, a description of which bacteria genus shared between fish species and within species should be presented. How many OTUs they share as well. Figures 2 and 3: a) rarefaction curves require the legend reflecting sample label.

In the supplemental figure S2, the final word to describe will be location or habitat?. Finally, PCO plot graph seems better to describe the differences between species and habitat instead of a NMDS. The R2 and stress value is not the strongest in both compared factors.
Additional comments: The manuscript is a well-written and useful summary of the current status of “data publication” from a certain perspective. The authors, however, need to be more analytical. This manuscript does an excellent job showing a new protocol that can be easily used to take fish gut samples in the field that can be used to gut microbiome analysis without using -80 oC to preserve the samples until further microbiome analysis. The paper would be both more compelling and useful to a broader audience if the authors provide a better picture of the factors that drove the gut microbial community in fish as well as the importance of the host’s physiology and health.


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: USE OF NEXT GENERATION SEQUENCING TO COMPARE SIMPLE HABITAT AND SPECIES LEVEL DIFFERENCES IN THE GUT MICROBIOTA OF AN INVASIVE AND NATIVE FRESHWATER FISH SPECIES
Review round: 2
Reviewer: 1

Output:
Basic reporting: The overall manuscript is good. The structure could be improved with a more in-depth literature review as noted. Some incorrect uses of references and is important homogenizes the terms like gut microbiota or gut microbiome along the document. Please check references and perhaps add some additional ones focused specifically on fish microbiomes in wild based on trophic habit and feeding strategies (i.e. The gut microbiome and degradation enzyme activity of wild freshwater fishes influenced by their trophic levels by Liu et al 2016). The tables and figures are ok.  The github page in the abstract cited by the author shows that nothing is listed. This needs to be available to reviewers during the review stage.
Experimental design: The primary research aim should be very clear: you proposed a gut microbiome analysis comparing two different species (feeding strategies and locations-which this part is missing), and only compare habitat within the same fish species (RG).

When they sampling the fish, they say the animals were euthanized within ~ 3 hours of capture; did they were kept together in the same container sharing the water during that time individually until euthanize and dissection?

Back in the preservation method, although NAP buffer showed some promising results in one study for mammalian samples (Camacho 2013), it does not mean it provides the same good preservation picture for fish gut digesta.

Line by line review
Line 173 correct the upperSt; line 318 punctuations; correct parenthesis in lines 443 and 727.
Line 732, never mention Cetobacterium somerae in the results (check this part)
For evenness should be calculated Shannon-evenness not only Shannon index line 781
Table 1 & 2 indicated in line 389 only shows one complete data set of coverage (description as well only say Table 1)
Validity of the findings: The calculation of alpha and beta diversity improves the results in the manuscript. There is some suggestion about how the alpha diversity index are presented. It would be better if the index results (figure 6 and 7) were presented on a table and diversity index like Simpson, and evenness index like Shannon-evenness could be added to it. How could you explain that the two different species didn’t show any significant difference among the 3 alpha diversity indexes?
Figure 3AB: What would be the main reason that samples of the eagle wings are less disperse than the governors island. It will be interesting determining the number of OTUs shares between habitat and species, as well which genera are the ones that are unique in each fish species.
Additional comments: With the changes made on the original manuscript clarify better the aim of it. The authors focused on pinpoint that there is significant difference between gut microbiome. Adding the PCO ordination, you can distinguish better a species effect and habit effect on GO based on samples collected with your method.


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: ANTIMICROBIAL ACTIVITY OF STREPTOMYCES SPP. ISOLATED FROM APIS DORSATA COMBS AGAINST SOME PHYTOPATHOGENIC BACTERIA
Review round: 1
Reviewer: 1

Output:
Basic reporting: There are several instances of incorrect English grammar in the manuscript. I have provided a list of what I observed below in the "General Comments" section.
Experimental design: There is no defined research question in the article. Instead, this article reports an observation that Streptomyces isolated from Apis dorsata honey and pollen exhibit activity against four Gram-negative plant pathogens. There is no indication as to why the authors chose to investigate the activity of bee-associated isolates against  phytopathogenic bacteria.

When constructing phylogenies, the authors should use maximum-likelihood approaches, instead of neighbor-joining approaches. See the "General Comments" section for further detail.
Validity of the findings: At the end of the Introduction, the authors state: "According to data obtained in the current study, the antibacterial activity of secondary metabolites from actinomycetes could be implemented against phytopathogenic bacteria to assist in crop protection worldwide." I believe that this is an overstatement of the findings presented in the manuscript. Though it is very likely that the activity against the phytopathogenic bacteria is due to production of secondary metabolite(s), the authors have not demonstrated conclusively that their extracts contain these compounds. Further, there is no assessment of the ability of these Streptomyces to protect plants from phytopathogenic bacteria in situ.
Additional comments: In this manuscript Promnuan et al. report the isolation of twenty-five actinomycete isolates from pollen, honey, and adult workers of the bee Apis dorsata. Of these twenty-five isolates, the authors identify three Streptomyces isolates (DSC3-6, DGA3-20, and DGA8-3) that were active against four plant pathogens (Erwinia carotovora, Ralstonia solanacearum, Xanthomonas campestris pv. campestris, and Xanthomonas oryzae pv. oryzae) in a cross-streak assay. Subsequently, the authors generated crude extracts from these strains and measured their minimum inhibitory concentration (MIC) against the four plant pathogens in vitro.

Comments

1.	Lines 176-7: The authors use MEGA version 6.06 and the neighbor joining (NJ) approach the generate phylogenetic trees of their Streptomyces isolates with other strains. This version of the MEGA software is from 2013. The newest version is MEGA X (Kumar et al. 2018. Molecular Biology and Evolution) version 10.1.8, which was released in April 2020. I would also recommend that the authors use maximum likelihood (ML) approaches to generate their phylogenetic trees, instead of NJ. The NJ algorithm is phenetic and does not consider evolutionary models, which are used by the ML algorithm. ML is available in MEGA X.

2.	Lines 214-7: Bootstrap support is not an appropriate measure for defining the closeness of a relationship between two organisms. Without measures, such as a genome scale phylogeny or average nucleotide identity across the genome, I would be hesitant to make claims on the “closeness” of the relationship between these isolates and other strains. That said, the specific identity of the isolates does not impact the other findings reported in the manuscript.

3.	Is there a link between these Streptomyces isolates from A. dorsata and the plant pathogens the authors chose to investigate? Inhibition of Gram-negative bacteria by Streptomyces is generally low. Is there specific inhibition of these plant pathogens or do these three Streptomyces isolates show more broad inhibition against other Gram-negative bacteria? How do the extract MIC values compare to other extracts from different Streptomyces?

4.	Paragraph 234: The content in this paragraph would fit better in the Introduction than in the Discussion section, especially given the ending sentence: “These reports indicated that actinomycetes, especially Streptomyces, may provide a new approach for the use of actinomycetes for biocontrol in agriculture.”

Minor Comments

Line 41: Include a hyphen between “Gram” and “negative”
Line 43: Add the “e” to “seed-borne”
Line 48: Remove “the” from “…vessel causing the yellow/white…”
Line 51: Remove the “s” from the end of “causes” in “…pathogen can causes disease…”
Line 114: The sentence “The actinomycetes were isolated from three hives of A. dorsata” is redundant with the information presented under “Sample Collection”.
Lines 113-22, 128, 134: Include recipes for the bacteriological medium used in the actinomycete isolation, plant pathogen cultivation, and bioassay experiments.
Line 166: Report the centrifuge speed in × g, instead of RPM
Line 167: Replace both instances of “were” with “was”
Line 179: Why was Streptomyces thermocarboxydus DSM 44293T chosen as the outgroup?
Line 183: Include a sentence indicating that the sequences were deposited into GenBank and their accession numbers.
Line 199: Remove the word “growth” in “…growth phytopathogenic bacteria…”
Lines 209-11: Rephrase the sentence to not use the verb “blasted”
Lines 234-7: Remove “such as antibacterial and antifungal compounds” or rephrase sentence to improve clarity.
Line 237: Remove “The” from “The actinomycetes…” and start sentence with “Actinomycetes…”
Paragraph 253: There have been several recent papers assessing the large scale antimicrobial potential of insect-associated Streptomyces that have not been cited here.


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: ANTIMICROBIAL ACTIVITY OF STREPTOMYCES SPP. ISOLATED FROM APIS DORSATA COMBS AGAINST SOME PHYTOPATHOGENIC BACTERIA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The English is mostly clear and could be improved in several sections throughout the paper:
•	Line 19 – The antimicrobial activity was not isolated so the sentence should read “The aim of this study was to investigate the antimicrobial…”
•	Line 21 – The manuscript describes three media used to isolate actinomycetes and the abstract says “four different media”
•	Line 81 – the phrase “and suggests” should be changed to “which suggests”
•	Line 85 – the word “always” should be removed as the authors list several different places the comb could be located
•	Line 86 – “and sometimes” should be changed to “or sometimes”
•	Line 88 – “never been studied and reported.” should read “never been studied or reported”
•	Line 99 – “bee” should be plural “bees”
•	Line 195 – “show potent activity” should read “showed potent activity”
•	Line 199 – “growth phytopathogenic bacteria” should read “growth of phytopathogenic bacteria”
•	Line 204 – The last sentence of the paragraph starting on this line is repeated almost exactly on lines 221-223. I recommend removing the sentence on lines 221-223
•	Line 208 – the word “potential” can be removed as the inhibition was apparent in the previous section
•	Line 211 – “blasted” should be changed to “analyzed by BLAST”
•	Line 226 – The sentence should be restructured to read “This study investigated antagonistic activity of actinomycetes isolated from the giant honey bee (A. dorsata), against phytopathogenic bacteria.
•	Line 230 – “study the actinomycete” should be changed to “study an actinomycete”
•	Line 231 – “activity for the growth” should be changed to “activity against the growth”
•	Line 234 – 16S rDNA should be changed to 16S rRNA to be consistent with the rest of the manuscript
•	Line 237 – The sentence beginning “The actinomycetes isolated” should be changed to “Actinomycetes isolated”
•	Line 261 – “bee” should be made plural to “bees”
•	Line 266 – “previous study reported” should be changed to “previous study we reported”
•	Line 271 – “antimicrobial product for” should be changed to “antimicrobial products for”
•	Line 274 – This sentence should be written “Bacterial bright leaf (BLB) disease, which is caused by X. oryzae pv. oryzae, is one of the major diseases of rice in Asian countries”
•	Line 276 – the word “studied” should be removed from “in vitro studied”
•	It is unclear what the authors mean by “greenhouse conditions” in line 280.

The relevant literature seems to be mostly referenced and sufficient background is provided in the introduction of the manuscript, however, the manuscript could be improved by drawing a clear distinction between use of Streptomyces strains themselves as biocontrol measures and the use of antibiotics isolated from  Streptomyces as treatment for plant pathogens:
•	Several times in the Discussion section it is unclear if the authors are arguing for the use of the strains they have identified as biocontrol agents themselves, as in line 252 or as sources of isolated antibiotics as in line 271 and 279. A clear distinction should be made between the two and the authors should clarify which approach they are proposing.

The article conforms to the structure suggested by PeerJ and the figures and tables are relevant to the text in the manuscript.

The results presented are relevant to the hypothesis being tested.
Experimental design: The research is presented in the manuscript is within the aims and scope of PeerJ.
The research question is very nicely set up in the introduction and the relevance of the research is made clear. It is stated in the manuscript that this is the first study to isolate Streptomyces with antibacterial activity against phytopathogenic bacteria from the giant honey bee.

Relevant controls are used in the experiments and replication was performed. Streaking the cultures from the microtiter plates onto nutrient agar plates during the MIC experiments provided extra validity to the experiment beyond simply checking for turbidity. The authors used the program MEGA version 6.06 to create their trees and perform their bioinformatic analyses.
•	MEGA is now running on version 10.04, as of 2018, and is free to download. The trees and bioinformatic analyses should be performed with the most up to date version of the software.
•	Additionally, the MIC values are reported in mg L-1 as opposed to the more commonly reported µg mL-1.

The methods are well described and rely on previously published protocols with minor adjustments that are described in the manuscript. The experiments could be replicated with access to the same strains.
Validity of the findings: The 16S rRNA sequences have been deposited into online databases and the experiments appear to be robust and controlled.

The conclusions require additional editing in the manuscript prior to publication.
•	The three Streptomyces strains capable of inhibiting the phytopathogens were not isolated from the giant honey bee, but were rather isolated from pollen (DGA3-20 and DSC3-6) and honey (DGA8-3). The title of the manuscript and the text throughout the manuscript state that the Streptomyces strains were isolated from Apis dorsata, but this is not reflected in the data, where the single strain isolated from Apis dorsata did not have inhibitory activity against the phytopathogens. This is relevant as a 2019 Nature Communications paper by Da-Ran Kim et al. found that an endophytic Streptomyces from the strawberry rhizosphere could be detected in pollen samples of the strawberry plants. This pollen containing the Streptomyces could then be carried by pollinating bees between flowers and had the ability to protect both the strawberries as well as the pollinating bees from pathogens.

 Kim, D., Cho, G., Jeon, C. et al. A mutualistic interaction between Streptomyces bacteria, strawberry plants and pollinating bees. Nat Commun 10, 4802 (2019).

The Streptomyces isolated by the authors may originate from plants that the bees were pollinating as opposed to the bees themselves. This must be addressed in the manuscript and the title of the manuscript should be altered to reflect this.
Additional comments: The authors have identified three Streptomyces strains associated with the giant honey bee and closely related to known Streptomyces species.  The strains and organic extracts of the strains have antibacterial activity against four Gram-negative plant pathogens that collectively cause damage to many crop species around the world.  The authors argue that the giant honey bee may be a source for the isolation of Streptomyces that produce agriculturally useful antibiotics.


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: ANTIMICROBIAL ACTIVITY OF STREPTOMYCES SPP. ISOLATED FROM APIS DORSATA COMBS AGAINST SOME PHYTOPATHOGENIC BACTERIA
Review round: 1
Reviewer: 3

Output:
Basic reporting: English needs to be reviewed.
The authors can use some more actual literature references.
The article has few figures to describe the work and did not present the raw data.
The results are relevant to hypotheses.
 I have a few suggestions for improvement as listed below.
- I recommend modifying the Abstract, adding the background, and reduce the information described of results.
- line 63 adds the reference after the sentence "The management of plant diseases is difficult."
- In lines 80 and 99, the authors rarely mention the efficacy of Actinomycetes associated with bees which a good antimicrobial in combating phytobacterial pathogens. I suggest that you improve the description and add more details on this topic?
- line 80 and add the reference.
- line 83 The authors started the descriptions of giant bees without any association with the phytobacterial pathogens. Please, reformulated this paragraph.
- Please adding the figure of the test of the screening of antagonistic actinomycetes is a very important part of this research.
Experimental design: The idea is original and the research question is relevant and meaningful.
 I have a few suggestions.
- After isolation of colonies was made morphological classification and microscopy images? Please, arrange it if not done.
- line 139-147 add the reference. What is the yield of this bioactive extraction protocol? It is important to indicate these values in the text.
- Why didn't you use bactericides, hypochlorite, formaldehyde solution, and antibiotic in MIC control?
-I suggest adding the figure of isolation of actinomycetes from A. dorsata in Supplemental files.
-  Add the Evalue and Percent Identity used for the selection of the Streptomyces sequences.
- In line 207 and 209 the authors described “using 16S rDNA”, and in line 209 and 212 you use “16S rRNA”. Please, standardize the information.
- In line 209 and 212 “The almost-complete 16S rRNA gene sequences”. This information can be removed, and leave only The 16S rRNA gene sequences.
- Add in Supplemental files the figure of CLUSTAL_X alignment.
- The image of Figure 1A is a different format from the others, please, put it in the same format.
- Why the author submitted the Figure1 in Supplemental files?
- line 234 describes more studies about Streptomyces secondary metabolites with antagonistic activity against phytopathogens.
- line 237 add the reference.
-  I suggested the reformulation of the Discussion topic, it is very important to associate the results obtained with those already described in the literature. Thus, the results do not make sense.
Validity of the findings: The discovery is really interesting, the results and discussion need to be improved to cooperate with the novelty described by 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: ANTIMICROBIAL ACTIVITY OF STREPTOMYCES SPP. ISOLATED FROM APIS DORSATA COMBS AGAINST SOME PHYTOPATHOGENIC BACTERIA
Review round: 2
Reviewer: 1

Output:
Basic reporting: Overall, the English used in the manuscript is clear. I have included some suggestions that could improve clarity of a few sentences (See Line Comments, below).

The literature references are sufficient.

All data is shared.
Experimental design: no comment
Validity of the findings: All underlying data have been provided.

There are several instances in the manuscript where it is specified that the actinomycetes were isolated from A. dorsata, which is not the case. The title has been changed to reflect that most isolates were from pollen or honey, but the text needs to be updated (e.g., Lines 123, 283).
Additional comments: Promnuan et al. report the isolation of 25 actinomycetes from the surface of adult workers of the honeybee Apis dorsata, honey, and pollen. Subsequently, the isolates were tested for antimicrobial activity against four plant pathogens with three isolates, later identified as Streptomyces by 16S rDNA gene sequencing, showing activity against all the plant pathogens.

In their revision, Promnuan et al. have addressed all of my initial comments. Below I provide one additional major comment and three minor comments. In addition, I have included line comments that may improve the clarity throughout the manuscript.

Major comments

According to Table 1, only one actinomycete was isolated from a honeybee, compared to 21 isolates from pollen and 3 isolates from honey. Further, the three isolates for which antimicrobial extracts were generated, were from honey and pollen, not the honeybee. Therefore, it is not necessarily fair to state that the actinomycetes were isolated from A. dorsata (e.g., Lines 123, 283). The manuscript title was changed, but the manuscript text needs to be updated accordingly.

Minor comments

Since the scientific name of Erwinia carotovora was updated to Pectobacterium carotovorum, then the references to E. carotovora need to be updated to P. carotovorum throughout the manuscript. (e.g., lines 41, 146, 173, 177, 217, 223)

All scientific names should be spelled out fully the first time that they are used (e.g., Lines 79-81, 102, 110, 113)

Lines 125-6: It is not yet valid to say that the antibacterial activities demonstrated in this manuscript are due to secondary metabolites.

Line Comments

Lines 26, 28, 98, 139, 221, 222, 224, 266: Insert a space between mg and L-1.

Line 32: Update the abstract to reflect the use of maximum likelihood approaches instead of neighbor joining for generating phylogenetic trees.

Line 78: The abbreviation BLB has already been defined.

Line 91: What was the similarity metric for 99.6%? 16S rDNA sequence?

Lines: 92, 96, 98: These lines describe strains with the highest/maximum inhibitory activity from different studies, but do not provide context for the comparison.

Line 145: Ralstonia solanacearum should be abbreviated to R. solanacearum

Line 209, 244: Replace ‘glycerol-asparagine (ISP5) agar)’ with ‘ISP5 agar’, given that this abbreviation was used in the methods.

Lines 224-5: This sentence would fit better in the conclusion section of the manuscript, instead of in the results.

Line 228: Did the authors mean to write ‘…showed inhibition of all four phytobacterial pathogens’ instead of ‘…all three…’ as they tested four different plant pathogens? (see line 216)

Lines 248-50: This sentence is redundant with lines 244-7.

Lines 250-1: Could the authors clarify this sentence? I am not sure what they are referring to.

Line 265: Delete the word ‘the’ from ‘…showed the activity’…

Line 281: Replace ‘Bacterial bright leaf (BLB) disease…’ with ‘BLB disease’ as the abbreviation was defined at line 46. Alternatively, delete the abbreviation at all three locations (lines 46, 78, 281) and use the full name ‘Bacterial bright leaf disease’.


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: ANTIMICROBIAL ACTIVITY OF STREPTOMYCES SPP. ISOLATED FROM APIS DORSATA COMBS AGAINST SOME PHYTOPATHOGENIC BACTERIA
Review round: 2
Reviewer: 2

Output:
Basic reporting: The English could be improved in several sections throughout the paper:
Line 31 - the word "sequence" should be plural "sequences"
Line 34 - The word "respectively" should be added at the end of the sentence to provide clarity
Line 229 - The authors are testing against four phytobacterial pathogens, not three
Line 275 - Change "from the in vitro screening method" to "in vitro"
Line 276 - Change "and reducing" to "and reduced"
Line 276 - "A pot experiment" is this an in situ experiment or in vivo?
Line 279 - The last sentence "Further investigation on potent actinomycete strains as biocontrol agents under greenhouse conditions" has no verb and is not a complete sentence. Additionally, it is repeated below in the conclusions section. It should be removed or edited.
Line 287 - The English in the last sentence should be altered. I believe it should read "In future studies, the potent actinomycete strains will be investigated as biocontrol agents with plants under greenhouse conditions."

Relevant literature seems to be referenced and sufficient background is provided.

The article conforms to the structure suggested by PeerJ and the figures and tables are relevant to the text in the manuscript.

The results presented are relevant to the hypothesis being tested.
Experimental design: The research presented in the manuscript is within the scope of PeerJ.

The research question is nicely set up in the introduction and the relevant research is made clear. The manuscript states that this is the first study to isolate Streptomyces with antibacterial activity against phyopathogenic bacteria from the giant honey bee.

Relevant controls are used in the experiment and replication was performed. The authors used up-to-date versions of their bioinformatic software.

The methods are well described and rely on previously published protocols with minor adjustments that are addressed in the methods section.
Validity of the findings: The underlying data has been deposited into the relevant databases.

The fact that the potent actinomycete strains were mostly isolated from pollen is addressed and this is reflected in both the discussion and the title. However, the English in the discussion section needs to be edited. The sentences beginning on line 251 and ending on line 254 are copied nearly directly from my previous review. While the sentences aim to provide context from the literature for the sentences following them, they do not make sense grammatically as they are written and should be written in the authors own words.
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: ANTIMICROBIAL ACTIVITY OF STREPTOMYCES SPP. ISOLATED FROM APIS DORSATA COMBS AGAINST SOME PHYTOPATHOGENIC BACTERIA
Review round: 2
Reviewer: 3

Output:
Basic reporting: The authors accepted all the suggestions made previously, improving the quality of the text.
Experimental design: I have a few comments to improve the text.

line 87  "soilborne" change to soil-borne;
In line 194 the authors wrote "After incubation, plates were observed visually. " why not use this method instead of the absorbance method?
line 203- Add the  time of centrifugation;
line 206- Add a reference;
line 208 - Describe what type of sequencing was performed. And add in the accession number of the sequences obtained from the tested isolates;
line 257- I suggest that the authors make a single phylogenetic tree for the 3 isolates, so it is easier to visualize and understand the result.
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: PERIPHERAL-PHYSIOLOGICAL AND NEURAL CORRELATES OF THE FLOW EXPERIENCE WHILE PLAYING VIDEO GAMES: A COMPREHENSIVE REVIEW
Review round: 1
Reviewer: 1

Output:
Basic reporting: I commend the authors for giving an overview over the literature on peripheral-physiological and neural correlates of flow during video gaming. I believe that psychophysiological methods represent a promising approach to both research on flow experiences in particular and on gaming experiences in general. Given the in part contradictory findings and different research methods and designs employed so far, I think that this literature review will greatly benefit the field by summarizing our current knowledge and state of the art. Considering the various possible applications of flow research in health-related areas and the focus on psychophysiological methodology, I further believe that this article will be of high interest for PeerJ’s readers. In terms of English language and grammar, the manuscript satisfies professional standards required by PeerJ and can be allowed for publication. However, I would like to see a major revision of the manuscript’s structure before publication as I found it at times confusing to read and hard to grasp the main information from the text. Therefore, I will now make detailed recommendation on how to change the reporting:
1.	When giving the definition of flow, processing fluency is not mentioned; however, apart from attentional absorption and intrinsic enjoyment, processing fluency should be considered a key dimension of flow (Csikszentmihalyi, 1975), from which many psycho- and neuropsychological hypotheses can be deduced. Therefore, the role of processing fluency during flow needs to be made explicit in lines 38-40, 46, and 120-124.
2.	The flow factors given in lines 45-50 should be ordered into antecedents and components: The main antecedent for flow is the optimal balance of skills and challenges (theory: Csikszentmihalyi, 1975; correlation: e.g., Jackson & Marsh, 1996; experiment: e.g., Keller & Blomann, 2008; meta-analysis: Fong, Zaleski, & Leach, 2015); therefore, I would like to see a small paragraph dedicated to it (maybe directly referencing the flow channel model), to the experimental approach it inspired (lines 82-90), and to personality traits that modulate its causal relationship with flow (lines 90-98). This way, a single paragraph would summarize the theoretical background for the experiments you are about to report. I also think the statement from lines 468-469 should be part of this introductory paragraph, so the reader knows right away about potential methodological limitations.
3.	Concerning the flow components, I suggest you group 2), 3), 7), and 8) together as they are all related to absorption. In contrast, 4), 5), and 6) are all related to fluency. At this point, it should be clarified that 4)-6) can both be regarded as activity characteristics and thus antecedents of flow, and as subjective perceptions during flow and thus flow components. Please also refer to Jackson and Marsh (1996), when giving these flow components since the differentiation between 4)-6) stems from their work. Also, include intrinsic enjoyment as another flow component, which is sometimes conceptionalized as an antecedent or a consequence of flow, too. This is important since some flow questionnaires measure intrinsic enjoyment as a flow component (e.g., Jackson’s flow scale).
4.	In regard to experimental approaches in flow research, both the dynamic matching of skills and challenges (which you refer to in lines 66-68; e.g., Keller & Blomann, 2008) and pre-testing skills to assign matching challenge levels (e.g., Moller, Csikszentmihalyi, Nakamura, & Deci, 2007) should be mentioned in addition to creating a medium challenge level (lines 85-90). I would also recommend to at this point briefly state the possibility of having more than three experimental conditions as some of the experiments you are about to report feature another condition (immersion; autonomy), which might confuse the reader later on. Moreover, I know the terminology is not used consistently in flow research, but I think the reader would greatly benefit from you establishing standards for your paper, i.e. stating something along the lines of “When the game’s difficulty is set to a high level, the gamer is assumed to experience stress, frustration, or anxiety rather than flow. In the following, we will refer to the corresponding experimental condition as the overload condition when describing the results of a flow experiment.” Please also make sure that you then use consistent terms throughout lines 120-527.
5.	I would also like to see a paragraph on flow measurement to early on give the reader an idea of how flow was assessed in the studies that you are about to report. In this paragraph, you should mention the ESM and flow questionnaires as direct, but retrospective flow measures as well as the dual task approach and physiological indicators as indirect, but non-disruptive flow measures. At this point, the limitations of assessing a state with retrospective self-reports should also be clearly stated, making the case for neural or peripheral-psychological indicators. Thus, please form a new paragraph on flow measurement from lines 69-73, 103-108, and 469-479. I would also prefer more references for flow questionnaires (line 73), ideally by adding a corresponding column to Tables 1-4.
6.	Lines 51-64 need to be marked more clearly as speculation or more evidence on the 'beneficial nature of flow on psychiatric symptoms' needs to be given. Also, a clearer explanation of the reasoning behind flow being beneficial in a clinical context should be provided. Otherwise, I would just leave it out altogether.
7.	In line 110, you refer to this manuscript as the first review of this kind. However, I am aware of at least one comparable review (Knierim, Rissler, Dorner, Maedche, & Weinhardt, 2018). Whereas I think, your work still adds valuable information and provides an important update, the other review (maybe there is even more?) should be referenced properly and the added value of your literature review should be explained.
Experimental design: I am confident that the manuscript cites relevant sources correctly and fulfills the methodological and ethical standards required by PeerJ. However, I believe improving the organization of subsections and of the overall structure of the manuscript is necessary to give the reader a clearer overview of the topic. Moreover, to ensure comprehensive, unbiased coverage, I strongly suggest to revise the methodological approach. Please consider my recommendations to improve the results section:
1.	In regard to the method used to collect papers on peripheral-physiological and neural correlates of flow during video gaming, I strongly suggest to follow PRISMA guidelines (http://prisma-statement.org, see checklist and flowchart). This would also help the reader to evaluate the study-selection strategy. Specifically, the combinations of keywords used should be made explicit (e.g., ‘neural OR correlates OR brain activity AND flow’) as well as all eligibility criteria. I am also not convinced that Google Scholar can be used to obtain a comprehensive overview and therefore strongly encourage to further use PubMed and Web of Science. Maybe more specific keywords pertaining to certain methods/indices and flow would also help to make sure all relevant papers are found. Just to give you an idea, from my own literature research I can name papers on flow and psychophysiology that you have not included in your literature review: Kivikangas (2006), Drachen et al. (2010), Gaggioli et al. (2013), Bastarache-Roberge et al. (2015), Colzato et al. (2018), Plotnikov et al. (2012), Peifer et al. (2014b), and Tozman et al. (2017). I believe it is crucial to revise your literature review to ensure that no invalid conclusions are drawn due to the lack of certain relevant papers.
2.	Whereas I find structuring your report into a subsection for peripheral-physiological and neural correlates of flow very helpful, I think the subsections themselves need to be structured more clearly. I suggest to start with a paragraph summarizing theoretical assumptions about flow and the corresponding measures like you did in line 266-280 for the neural subsection. For the neural subsection, you mention the hypofrontality hypothesis (lines 273-274, 358-359) as well as synchronization theory (lines 275-280); however, I would in the same paragraph also mention the notion of effortless attention (lines 568-571), peak performance (lines 130-131, 378-380), and the flow components loss of self-awareness, attentional focus, and intrinsic enjoyment (please make sure to use a consistent terminology here as you also call the latter concentration or intrinsic reward at times), since they, too, inform about potential neuronal correlates of flow. That would help the reader understand which neural correlates are to be expected before learning the actual results. Please note that the link between flow and peak performance should be brought up and explained (!) already in the introduction, preferably when you write about processing fluency and optimal challenge. As of now, it comes a bit out of nowhere when it is used to explain certain results, which is a good example of what I mean by 'confusing to read'.
3.	Similarly, I would recommend expanding on the theoretical background of peripheral-physiological flow correlates in a separate paragraph before presenting results. Please include the inverted U-shaped hypothesis by Peifer et al. (lines 181-184, 539-544), De Manzano et al.’s conceptualization of flow as a state of positive affect and high arousal (lines 160-162; you call it effortless attention but as far as I know De Manzano speaks of arousal and Bruya (2010) speaks of effortless attention, so that should not be confused), and the notion of co-activation of the parasympathetic and sympathetic system during flow (Ullén, De Manzano, Theorell, & Harmat, 2010) in this paragraph, as well as briefly effortless attention and peak performance as these two will reappear in the neural subsection. At this point also comment on assumptions about flow and high arousal/stress (lines 124-127), but please clarify right in the beginning that this is presumably highly dependent on the activity context. You bring up task-dependency only in the neural subsection in line 324, but it applies to all psychophysiological results and should be emphasized right in the beginning!
4.	In addition to presenting the theory in a clearer manner, I would also appreciate a clearer presentation of the indicators themselves. Even though PeerJ’s readers will most likely be familiar with psychophysiological indicators, you present a broad variety of methods from eye-tracking to tDCS in this literature review, so readers may not know about all of them. As of now, you explain some indicators when you present corresponding results (e.g. LF-HRV, lines 146-149), but I would like to see this done consistently for all measures employed (peripheral-physiological subsection: HR and HRV, EMG, cortisol, respiration, EDA, and eye-tracking; neuronal subsection: fMRI, perfusion MRI, fNIRS, tDCS, and EEG). Please make sure to refer back to the theory paragraph when you introduce the measures (e.g., cortisol, HPA-axis, stress, Peifer’s hypothesis), so that the reader knows right away how each measure can be related to flow experiences. I would suggest writing a separate paragraph on all indicators and placing it after the theory paragraph, before all results are reported, or writing a short disclaimer for each indicator before presenting the results for this indicator.
5.	Please also reconsider the organization of your report of results: You seem to organize the studies according to when they were conducted; however, given the many different methodologies employed, I would recommend to organize them according to a) the indicators assessed or b) the theoretical background. Depending on which one you chose, the other one should be used to form subsections within the paragraph (e.g., if you choose to go by indictors, first present all evidence this indicator provided on for instance the effortless attention hypothesis, then on the arousal hypothesis, and so on… or the other way around. But keep this structure throughout the report. This is crucial as for instance in line 179-180 you draw a conclusion from the results you just reported and later on state that other results contradict this conclusion; however, it should be made clear within the same sentence or at least paragraph whether a conclusion can be considered valid or not as readers who only scan the text could otherwise pick up wrong information.) This also means that some studies might be brought up several times as they include different indicators or hypotheses – in that case the method should be explained in detail the first time and only briefly referred to from then on. For the sake of clarity, though, it would be very convenient for the reader to get all the information we have on a certain indicator or hypothesis in one single paragraph, instead of having to switch back and forth. Similarly, when you report EEG results, I would like to have different paragraphs/subsections dedicated to results on each frequency band.
6.	Please carefully check lines 120-527 in regard to how you report the studies’ methodology. This should always include the name of the game stimulus, the experimental design/conditions or a statement that the study was correlational, and ideally the name or information on the flow measure (or its proxy). In doing so, you can also refer to your tables. In case no proper flow condition or flow measure was used, this should always be pointed out and briefly discussed to inform the reader about potential limitations.
7.	I found that for some studies you do a very good job in relating results to hypotheses (e.g., lines 312-314, 430-436), but please really spell out the theoretical background (e.g., name the flow component that can be used to explain the result). Moreover, make sure that you do this for each of the reported studies in a similar way. I also really liked the format in which you presented the link between a theoretical construct and a physiological structure in lines 521-524 (putting the latter in parenthesis behind the former), so maybe use that more thoroughly.
8.	I believe that certain results need clearer explanations on your part: the contradicting results on flow and arousal levels (which you also sometimes call tension or stress – again please use a more consistent terminology; lines 192-199); the meaning of LF-HRV (lines 146-147, 563-564; you do not bring up the substantial evidence that this may not be a direct indicator of sympathovagal balance after all except for one sentence in the discussion!; e.g., Reyes del Paso, Langewitz, Mulder, Van Roon, & Duschek, 2013)); flow condition/measure proxies and their limitations, see above (please be very careful with the wording here as for instance line 386 could be misunderstood as you confirming that high performance works as a proxy for measuring flow with a questionnaire).
9.	The concept of immersion is brought up in the report of certain studies (lines 150, 400-402), but is never clearly defined (with references no less) and contrasted to flow. I believe this concept is still way more prominent than flow in virtual reality and gaming research, so I would like to actually see a small paragraph in the introduction dedicated to it and to its relationship to flow. This will help gaming researchers to connect with your paper and readers in general to understand studies that distinguish a flow from an immersion condition.
Validity of the findings: I believe that the conclusion drawn in this literature review are well developed and supported. I only have minor recommendations to clarify parts of the discussion:
1.	I would suggest that you rename and restructure the subsection of your discussion according to the main hypothesis that will now be outlined in the theory paragraphs beforehand: arousal, effortless attention, hypofrontality, intrinsic enjoyment, and loss of self-awareness. This might require some changes to the structure as for instance effortless attention refers to your discussion of both findings on mental effort (lines 536 onwards) and attentional control (lines 595 onwards). I am certain that this will help the reader evaluate the in part contradictory findings.
2.	I would like to see additional brief subsections on methodological conclusions: In lines 551-559, 679-681, 639-656 and 668-691 you nicely discuss the limitations and applications of certain methods in this research area. I believe that these are very important take-home massages for future studies, so these considerations should be expanded on and stressed by dedicating an entire paragraph of the discussion to them. Also, please make recommendations for future research more explicit. Since task-dependency seems to play an important role for this line of research, it should be discussed in some detail.
3.	Similarly, one of the main conclusions I would draw from the research so far is what you state in lines 580-583 in connection to task-dependency. I think that this deserves a separate paragraph since it affects what can be considered a tangible research goal for future studies. I would also like to see it discussed more: What does that mean for psychophysiological flow and gaming research? If there probably is no such thing as a psychophysiological standard pattern for flow, why still study flow with psychophysiological methods? You may also want to consider Knierim et al.’s conclusion that only a co-activation of the parasympathetic and sympathetic system might serve as an objective indicator for flow experiences before completely debunking the possibility to find standard flow patterns, or come up with similar conclusions of your own.
4.	I have gotten the impression that at times flow and absorption need to be differentiated more clearly. In lines 590-594 you discuss this in relation to automaticity and in lines 664-670 indirectly in relation to attention. However, I think that it needs to be clarified to the reader that high automaticity (which I for the sake of consistency would call effortless attention) can be achieved also under less than optimally challenging condition in overlearned tasks. Similarly, attentional focus can be high also with high challenges if a person is motivated and purposefully concentrates on the task at hand. This should be taken into consideration when discussing corresponding results. In how far does this for instance represent a potential limitation for dual-task designs? I would also like to see it discussed in general, maybe also in relation to immersion: Can we differentiate flow from absorption or immersion in terms of underlying physiological patterns?
5.	The usefulness of performance as an indirect measure for flow, which is discussed in lines 670-679, should be marked more clearly as speculation. Ideally, I would also appreciate more references on the relationship between performance and flow, specifically in the field of computer gaming. Please keep in mind that the most straightforward conclusion is still that performance will be better for easier tasks, whereas flow requires a challenging task. The seemingly paradoxical thought that flow is related to peak performance needs to be explained properly (also already in the introduction, see above).
6.	I think the conclusion presented in lines 582-583 needs clarification. I find the wording “to some extent” very vague without further explanations.
7.	A minor observation, but please do not refer to flow as a feeling (line 664), but consistently as an experience or state.
Additional comments: 1.	Please note that in line 582 it says Peifer (2012); I believe it should be Peifer (2014).
2.	In regard to your tables, I was wondering why you sometimes use parenthesis when giving the m/f behind the sample size to indicate the sample’s gender distribution and sometimes you do not. If there is no reason to do this, I would prefer a more consistent style.
3.	Similarly, in your tables you sometimes indicate missing information with a blank space or with a dash (two dashes actually – maybe make it one longer one instead). Please stick to a consistent style.
4.	When you summarize conditions under design, you sometimes use capital letters in the beginning and sometimes not. Please also again consider using a consistent terminology whenever possible (e.g., ‘Overload’ instead of ‘Hard’, ‘Boredom’ instead of ‘Slow’, etc.). Sometimes the ‘/’ inbetween conditions got shifted to the beginning of the next line, which should be avoided.
5.	You use both ‘and’ and ‘&’ in your tables, but sometimes the ‘&’ is placed in the beginning of a new line. Either spell out ‘and’ consistently or if you use ‘&’ make sure that it does not shift into the next line as this should be avoided in written English.
6.	When giving the time frame under design, you sometimes write out ‘x minutes gameplay’ and sometimes just ‘x minutes’; please use a consistent style.
7.	At times, there seem to be free lines or broader spacing in your tables; please stick to one line spacing throughout all tables.
8.	Beware that I am not a native speaker myself, but I am fairly certain that when giving time frames hyphens and ‘long’ are not used (e.g., ‘2 min’ or ‘2 minutes’ instead of ‘2-min-long’). Please revise your tables accordingly. Also, make sure you stick with either ‘2 minutes’ or ‘2 minute’.
9.	When listing more than two measures, a comma should be used before the ‘and’. Again, revise your tables accordingly, please.
10.	Table 1 seems to be missing the study of Mauri et al. (2011), which is cited in the text. Please make sure that each study is both described in text and appears in the corresponding table!
11.	In the table note for Table 1, I would like you to add explanations for the abbreviations fMRI, fNIRS, and NIRS since they appear in this table. I would also like to encourage a more consistent terminology even though I am aware that in the papers themselves different terms are used; you might consider using one term in regard to cortisol/cortisol level and EDR/GRS, EDA/GSC (and then of course also use it consistently in case it appears in another table). One minor formal observation: there is a blank in the wrong space between the GSR and BP explanations.
12.	In the table note for Table 2, you do not give explanations for the abbreviations fMRI, fNIRS, ECG, EDA, NIRS, PET, and tDCS. I believe each table should be understandable in its own right, so that a full explanation of all abbreviations is required for each table. Please also note that you write both ‘FNIRS’ and ‘fNIRS’, but it would be preferable to stick to one style of abbreviation.
13.	In the table note for Table 3, an explanation for the abbreviations EEG is missing. Please also again consider using consistent terms for electrodermal indices.
14.	In Table 3, there is a spelling mistake for ‘seconds’ when Wolf et al.’s study is presented.
15.	In Table 4, you start using a ‘+’ to add the dual task; I think it is a bit unfortunate to use a mathematical sign in a non-mathematical way, so maybe just stick to either using ‘and’ or ‘&’ (but consistently please, also in regard to the other tables).
16.	The table note for Table 4 is missing; however, again all abbreviations used in the table should be explained.
17.	One more minor observation: the font changes in Table 4 when Huskey et al.’s game is described.


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: PERIPHERAL-PHYSIOLOGICAL AND NEURAL CORRELATES OF THE FLOW EXPERIENCE WHILE PLAYING VIDEO GAMES: A COMPREHENSIVE REVIEW
Review round: 1
Reviewer: 2

Output:
Basic reporting: I have appreciated the effort of the authors to write a comprehensive review about the physiological and neural correlates of flow experience (while playing videogames). Authors stated that this is the first review include the studies about physiological and also neural correlates of the flow experience. This is maybe true but I have several questions and problem about about the concept and the purpose of this review. In my opinion neither the studies of the physiological nor the neural correlates of the the flow experience have not discussed in deep way. In my general opinion, this review is still not ready to publication because of several weaknesses and I can not see what this review add to the field. I suggest major revision or re-submission to the editors for this work.
Experimental design: The selection method for the review is poorly reported. Authors should provide detailed description about the combination of the keywords, how many article were find, the inclusion and exclusion criterias to final selection of the articles have  not reported in the review. I suggest the author to report their review selection method in details.
Validity of the findings: Validity of the results
The authors reported several studies on the field without applying their deep critical opinions about the results and suggestions for future research. Authors suggested  poor conclusions to summarize the studies about the physiological correlates of the flow experiences e.g. ”results are inconsistent…” OK, all the experts on the field can agree with this. What is major problem to find specific patterns for the underlying physiological and neural mechanisms of the flow experience based on the current literature? What are the author’s suggestion for future research to improve the field? I think some book chapters discussed the problem in more detailed and comprehensive way and this knowledge should be integrated into this paper also (Tozman & Peifer et al. 2016; Keller et al. 2016). It was interesting to read the studies about the neural correlates of the flow experience. I have no knowledge any other review artcile on this field. On other hand, the results was not discussed in good details and I would like read more about the different approaches and studies on this field. In addition, I don’t understand the concept and purpose of the review. If the authors aimed to review the physiological and neural correlates of the flow experience in one article I would appreciate some discussions about the connection between two fields. What we can learn to understand more about flow if we scope together the psysiological and neural correlates of the flow experience? What are the future directions in flow research to understand the connections between the neural correlates and the specific peripheral-physiological patterns of the flow experience??
Additional comments: I suggest to re-think the concept of the review. Maybe it would be enough if the authors just focus on the neural correlates of the flow experience with some critical review on the existing studies and add some suggestions how the reserach should be developed. This would really increase the validity of this paper and may fill some gaps on our field. If still the authors want to keep the peripheral-physiological part of the paper I suggest that make deep discussion about the question why the existing results are inconsistens.
Some minor comments
However most of the flow studies was made on computer gaming there are several studies was made on other tasks e.g. De Manzano 2010, Peifer 2014. Based on  the title of the paper the authors focused on studies on computer gaming and flow. This problems relates to confusion about the review selection method and also the concept of the article.
Authors only introduce an eight dimension model of flow. I suggest to introduce the nine dimension model by Csikszentmihalyi 1990 that was also used in FFS-2 scale  (Jackson & Eklund, 2002) and add autotelic experience (enjoyment) as a dimension. Athuors metioned that in several context in the text ejoyment is an important factor for computer gaimg in connection with flow.
References:
Tozman & Peifer (2016) Experimental Paradigms to Investigate Flow-Experience and Its Psychophysiology: Inspired from Stress Theory and Researc In: Harmat, L., Orsted, F., Ullén, F., Wright, J., Sadlo, G., (eds): Flow Experience: Empirical Research and Applications. Springer, 2016.
Keller, The Flow Experience Revisited: The Influence of Skills-Demands-Compatibility on Experiential and Physiological Indicators. In: Harmat, L., Orsted, F., Ullén, F., Wright, J., Sadlo, G., (eds): Flow Experience: Empirical Research and Applications. Springer, 2016.