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: SEQUENCE VARIANT ANALYSIS OF RNA SEQUENCES IN SEVERE EQUINE ASTHMA
Review round: 2
Reviewer: 1

Output:
Basic reporting: I mentioned in my last review that the authors consistently imply that there is an association between the two variants of interest and asthma when no statistical tests were performed.
1.	In some ways this has been addressed. However, there are some notable exceptions.
2.	Example:
a.	No association was found for allele or genotype frequency of the variant in the PACRG gene and asthma (p=1.0 and p=0.2).
b.	However, the authors still suggest that with a larger sample of individuals "the difference in frequency of the PACRG heterozygous genotype between asthmatic and non-asthmatic horses may increase."
c.	I mentioned last time that the allele and/or genotype frequencies were likely not stable with the sample sizes reported. Why do the authors report a trend to a future experiment when the statistical test is not significant, and the number it is based on might not be stable?
d.	Sentences like this need to be removed or changed.
Experimental design: The purpose of this study was "to determine the utility of RNA-Seq to call gene sequence variants, and to identify sequence variants potentially associated with asthma". I will focus my review on these two aspects.
1.	the accuracy of RNA-Seq data to determine DNA genotypes
2.	the variant enrichment procedure and their association to asthma
We will focus on the second aspect in this section:
During the last revision I focused on the lack of statistical power and statistical tests to determine if SNPs or RNA expression was associated to asthma.
1.	Now, the authors have performed statistical tests to determine the strength of association for (DNA) altered allele frequencies and altered genotype frequencies to asthma for two SNPs of interest (one in PACRG and one in RTTN).
2.	Although these statistical tests were performed, it is difficult to trust the authors variant enrichment procedure to select these two variants.
3.	Additionally, multiple testing correction was not considered as previously requested.
a.	The variant enrichment procedure (for variants of interest) starts by using 26,619 and 24,527 variants pre- and post- challenge in asthmatic horses and, 28,909 and 28,451 variants pre- and post- challenge in non-asthmatic horses.
b.	Of these variants they called "consensus sequence variants" within each group pre-asthma, post-asthma, pre-non-asthma, post-non-asthma, were called with SeqMule.
c.	Now I assume that they filtered the consensus variants per group to only consensus sequence variants unique to the asthmatic group pre- (2823) and post- (1788) challenge.
i.	This step is only mentioned in the Result, line 213: "The GATK variant calling and filtering workflow yielded 2823 and 1788 sequence variants present specifically in the asthmatic group pre- and post-challenge, respectively (Suppl. Figure 1)."
1.	Please add this to the methods (around line 165 or so) and clarify if these numbers were from consensus sequence variants per group, when exactly this filter was applied, and if the variants needed to be unique to each group.
ii.	If this step was performed, this by-passed much of the multiple testing correction burden.
iii.	By calling consensus sequence variants (I'm still not sure if they are calling consensus nucleotide or consensus genotypes) they are calling variants that are the most frequent in each of the four groups. Then the authors only use consensus variants that are unique (I think unique because they made a Venn diagram, this is not explicitly stated) to asthmatic pre- and post- groups. This filter enriches for variants that will be associated with their desired alternative hypothesis.
iv.	The authors should not enrich for SNPs that will agree with the their alternative hypothesis prior to statistical analyses. Example: in a GWAS researches do not enrich for SNPs associated with their dependent variable prior to the analysis to reduce the multiple testing correction burden.
v.	However, they could filter variants based on detrimental protein effects (the next step) prior to statistical analyses.
d.	Then I guess the authors use VEP and SIFT to identify variants that might affect protein structure. However, they do not state how many impactful variants are removed or kept by this filter. However, I assume that it is >=10 but <= 4611 (2823+1788).
e.	After this step the authors enrich for variants present in all asthmatic individuals and not present in all non-asthmatic individuals which leaves them with 10 variants (again enriching for variants that will agree with the alternative hypothesis). Then by 'manual verification' 8 of the 10 variants are excluded and they are left with their two variants of interest in PACRG and RTTN.
i.	How are 80% of these variants excluded? Were these 8 SNPs genotyped incorrectly? This is disconcerting.
The variant enrichment procedure would greatly benefit from a flow chart depicting methods. Did I misinterpret these steps?
At a minimum the authors should have performed a statistical association with the asthma phenotype for some X number of SNPs, followed by multiple testing correction for these X comparisons, as mentioned in my previous revision.
This is important as the authors results conclude that there is a significant association between altered allele frequencies for the variant in RTTN p = 0.042 and asthma. However, after a Bonferonni correction for multiple comparisons of only two tests (required alpha = 0.05/2 = 0.025) this is no longer considered significant. Notably, in the current version of the paper two tests were performed for the two variants of interest.
Validity of the findings: The authors only validate two of the RNA-seq SNPs with Sanger sequencing (in ~24 individuals). Since this is a main objective of the paper I expected more than two of the ~35,000 variants (I summed the numbers from the Venn diagram) confirmed. Therefore accuracy measurements of the RNAseq data to call DNA genotypes/SNPs is questionable.
Although it is good that the authors verified these two variants of interest with sanger sequencing.
I worry that the by enriching for variants that will tend to agree with their alternative hypothesis prior to testing improperly bypasses the multiple testing correction burden and is leading the authors, and potentially others to be more interested in these two variants than they should be. I am worried that the lack of statistical association to asthma is being disregarded to some extent, and therefore the relevance of asthma to these two variants is being inflated. If they state that there is a significant association to asthma for RTTN, then they should be held to the same statistical standards of other groups. Of course, it is possible that these variants are relevant to asthma, however, it seems that the statistics do not strongly support this conclusion when considering multiple testing.
Additional comments: The genotypes were called for 26,619 and 24,527 variants pre- and post- challenge in asthmatic horses, and 28,909 and 28,451 variants pre- and post- challenge in non-asthmatic horses.
1.	Line 165: The authors conclude that the "Difference in sequence variants before and after challenge were likely attributable to difference in gene expression, as previously discussed (39)."
2.	Why would the difference in the number of SNPs pre- and post- challenge be discussed in their differential expression paper cited? I did not find any variants called in citation 39.
3.	The difference in variants identified pre- and post- challenge are likely due to differences in alternative splicing, allele-specific expression, or simply a change in gene expression due to a time. The total quantity of RNA molecules expressed (as discussed in citation 39) is somewhat irrelevant when trying to justify the difference in variants called pre- and post- challenge. Rather, the total number of RNA molecules expressed can change due to allele specific expression etc.
4.	I don't believe this was appropriately presented in the text. This should be discussed as a limitation.
5.	Another thought, the difference in the number of sequence variants shown in the Venn diagram is likely very misleading if I interpret the methods correctly. They called "consensus sequence variants per group" and therefore I assume the most frequent (genotype or base-pair) was selected per group. This does not mean that the sequence variants were absent from the other groups, but rather that it was not the most frequent. Therefore, by choosing the most frequent (consensus) variants per group they might be inflating the differences between groups. Is this correct?

Line 172-173: what are existing sequence variants?
	"existing sequence variants were excluded"

What was the minimal depth required for calling variants?

Please consider adding a dedicated limitations section.


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: SEQUENCE VARIANT ANALYSIS OF RNA SEQUENCES IN SEVERE EQUINE ASTHMA
Review round: 2
Reviewer: 2

Output:
Basic reporting: The revised manuscript is, as previously, clearly presented.
Experimental design: The experimental design has been improved in response to the reviewer's comments.
Validity of the findings: The main criticism of the previous reviewers was the over interpretation of the results of the variant identification with respect to asthma, give the clear lack of statistical significance in variant frequency between groups. Throughout the revised manuscript the authors have toned down the conclusions in line with this.

The paper in now more appropriately focussed as a proof of principle for using RNAseq in horses to identify variants for future studies of the genetics of asthma and other conditions.

While this limits the significance of the results presented to the research community, it improve the technical accuracy of the manuscript.
Additional comments: No additional comments


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

Input:
Title: EFFECTS OF RHEUMATOID ARTHRITIS ASSOCIATED TRANSCRIPTIONAL CHANGES ON OSTEOCLAST DIFFERENTIATION NETWORK IN THE SYNOVIUM
Review round: 1
Reviewer: 1

Output:
Basic reporting: This is an  interesting manuscript which gives ue a lot information about the effect of inflammatory synovium to osteoclast formation. The manuscript is writen in quite professional English, gives sufficient introduction and background to support the work, as well as references. As for results, the authors provide 16 figs and tables, respectively.
Experimental design: The authers got the original data on gene expression, pathways and protein interactions related to rheumatoid arthritis from literature and databases namely Gene Expression Omnibus, KEGG pathway and STRING, and created a network for the differentiation of osteoclasts.
Validity of the findings: NF-κB pathway is well known to related with RA, no matter synovium or osteoclast, as well as TLRs, TGF-β， so this paper is lack of innovativeness.
Additional comments: The role of synovium on osteoclast is still unclear, we don't know inflammatory synovium induce osteoclast differentiation or osteoclast activation leads to synovium inflammation. This paper analysed the related signaling pathway in inflammatory synovium which would have a potential effect on osteoclast activation, interesting bioinformatics work and gave some information to investigate the relationship between synovium and osteoclast. But the problem is that the findings in this manuscript was something well investigated to be key proteins and pathways in osteoclast differentiation, maybe inflammation synovium will induce osteoclast, but needs more works to comfirm.


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

Input:
Title: EFFECTS OF RHEUMATOID ARTHRITIS ASSOCIATED TRANSCRIPTIONAL CHANGES ON OSTEOCLAST DIFFERENTIATION NETWORK IN THE SYNOVIUM
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comments. Please see general comments to author.
Experimental design: No comments. Please see general comments to author.
Validity of the findings: No comments. Please see general comments to author.
Additional comments: Manuscript 27887v1
Effects of rheumatoid arthritis associated transcriptional changes on osteoclast differentiation network in the synovium

In this manuscript by S. Harshan et al, the authors perform a bioinformatics investigation of gene expression in Rheumatoid Arthritis synovium based on publicly available data. The aim is to further understand the complexity of pathology in inflamed joints and how this could be targeted by therapy. The strategy is interesting, but the manuscript needs to be improved in terms of presentation in order to convincingly convey the conclusions. The study presented may be interesting for researchers in the field of rheumatology, but considering that few of them are bioinformaticians, the paper, in addition, needs clarification and more background information.

(a) The manuscript should have an abbreviation list.
(b) The authors should provide a figure with a flow chart of the work; the rational for using certain databases and algorithms, selection criteria (inclusion and exclusion) in each step, and better explain the interpretation of the networks created. For instance, why was the category “metabolism” not considered in the KEGG database? Why did the authors decide to identify proteins binding to DNA (line 161-162)? etc.
(c) Although this is not a review article, in order to make it easier for readers not completely familiar with the bioinformatic tools, the authors may add a “toolbox” explaining the different databases and their features. It is briefly explained in the text, but the manuscript would benefit from having this information also in a condensed way.
(d) The Supplementary tables need self-explanatory headings.
(e) The Supplementary figures should have legends explaining what is shown in the figures. In general, all Figure legends should be improved in order to better explain the figures.
(f) line 42-43: “Studies have used pathway analysis to identify affected pathways from lists of DEGs” This statement should be followed by references.

Results:
(g) line 185: only STAT1, IL7R, IGKC were upregulated in all seven datasets. This should be elaborated on in the Discussion part. In general, the origin of the data sets should be more critically considered and discussed. It says in line 186 “indicating the heterogeneity of the disease”. Is it rather the heterogeneity of the data sets? It is important to know more about the data sets in order to appreciate, for example, the downregulation of the AP-1 proteins in some of the datasets, but not all of them.
(h) in line 194 is written “two pathways were new” Is new compared to what? In what context? Many parts in the text leaves the reader with questions like that and the authors have to make a thorough editing in order to make the text clearer, and hence, easier for the reader to appreciate the interesting and important parts.
(i) line 209: the authors should explain what is meant with “affected” pathways?
(j) Table 3: How are the listed pathways ordered?
(k) lines 227-230: if known, the authors should comment on whether all patients with more than 10 years of disease still had active synovial inflammation.
(l) Table 5 could be taken out and the information written in the text.
(m) Figure 6: the content and text are very small. In addition, as with all figure legends in this manuscript, the text needs to be more explanatory. It is very difficult to overview what is shown in the figure. Could the data be shown in a different way?
(n) line 256:  the expression “up process pathways” needs to be expressed in a way so that it becomes immediately clear for the reader what is meant. This type of expression can be found in other parts of the manuscript as well and should be edited.
(o) what is written in lines 256-257 needs editing to become more understandable.
(p) Towards the end of the Results part, the text is becoming very unclear in many parts:
-line 277: What is meant by a “disruption in several signaling pathways”?
-line 287: “The protein Ubiquitin was found to have the highest degree…” Please explain “highest degree” (of what?)
-line305: “We removed the three smaller connected components…” Please remind the reader of what those components are, or refer to figure.
-line 354-55 “Figure 8 depicts….” Please better explain the “REL activation by PKC through BCL10-MALT1-IKK”. It is difficult to extract the thoughts behind this statement from the figure only.

(q) It is strongly recommended that the parts below are moved to the Discussion. I would also recommend a thorough edition of the text in the results part in general. Many sentences and statements are left without explanations.
Move to discussion:
-	Lines 201-207
-	214-223
-	294-304
-	355-379

(r) Discussion:
- It is recommended that the authors discuss and speculate about the reason for downregulation of signaling pathways in relation to the results.
- lines 428-430: ”The examination of the enriched GOBP terms of the network showed an involvement of T cell receptor signaling pathway, B cell receptor signaling pathway, Fc-ε receptor signaling pathway and NF-κB signaling pathway in the differentiation of osteoclasts in the RA synovium.” The involvement of for instance T-cell receptor signaling in osteoclast differentiation is somewhat challenging and needs to be explained/discussed. It is difficult to understand whether the results are referred to the synovia or to osteoclasts in different parts of the mansucript. Similarly, from lines 454-456 it is important to discuss how PRKCZ is involved in osteoclast differentiation (through T-cell signaling?)
-please discuss strengths and weaknesses of the strategy used in the presented study. In addition, would a discussion on the possibility that drug treatment is influencing the reported gene expression be important and interesting. Would it be possible to group data from patients on different treatments?

(s) The conclusions need to be stated in a more concise way.


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

Input:
Title: EFFECTS OF RHEUMATOID ARTHRITIS ASSOCIATED TRANSCRIPTIONAL CHANGES ON OSTEOCLAST DIFFERENTIATION NETWORK IN THE SYNOVIUM
Review round: 1
Reviewer: 3

Output:
Basic reporting: The article is well written and the language is clear. However, the description of the PPI network (lines 283-397) is too descriptive and difficult to follow. Genes and connections are described one after the other without much context. It will be better to simplify these sections and discuss examples most relevant to the current study.

Fig. 6 is too complex and aspects of it are unnecessary. It will be good to simplify it to only keep the parts that are discussed in the paper.
Experimental design: The methods related to GO enrichment analysis in PPI network is unclear (lines 160-170). Did the authors use GO terms corresponding to all the proteins in PPI for enrichment analysis?

Authors combined GO terms to build custom set for enrichment analysis (lines163, 166). It should be evaluated that this did not induces a bias in the analysis, e.g. using permutation analysis with appropriate random sets or other similar methods.

The pathway level analysis using KEGG to identify up/down-regulated pathways is based solely on the enrichment of the genes. Enrichment of upregulated genes in a pathway does not imply that the pathway output is also up, and vice-versa, without taking the information on repression/activation. Have this been taken into account? It should be clearly assessed if the pathway output is up/down.
Validity of the findings: The findings of this meta-analysis will be valuable for the readers in the field. However, it is not clear to me what is achieved using the PPI network that is not possible otherwise. Maybe the message is diluted in the verbose nature of the PPI description. Focussed writing and highlighting the novel findings in this analysis will certainly help.
Additional comments: No comments.


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

Input:
Title: EFFECTS OF RHEUMATOID ARTHRITIS ASSOCIATED TRANSCRIPTIONAL CHANGES ON OSTEOCLAST DIFFERENTIATION NETWORK IN THE SYNOVIUM
Review round: 1
Reviewer: 4

Output:
Basic reporting: no comments
Experimental design: no comments
Validity of the findings: no comments
Additional comments: Comments for Shilpa et.al:
In present manuscript authors have utilized published microarray data of synovial cells from patients with RA. Authors curated  the available database of GEO, KEGG and STRING compared with enriched genes from the RA microarray studies. With their analysis they come up with canonical NF-κB activation and osteoclastogenesis effected by NCF complex through ROS as a major pathological pathways in RA synovium. Study seems suitable for PeerJ readers and provides interesting tools to study available large public database for RA as well as various other conditions.
Following are my major concerns:
1.	Table 1 should include further details about published 7 studies which are the base for the current manuscript. Please include the cell type used, age distribution, cohort, gender/distribution, and most importantly major out-come from the microarray data as they have proposed. Later emphasis should be given that how Shilpa et.al analysis have novel findings compared to these public databases.
2.	Further these points should be discussed during the explanation of discrepancies when there is minimal overlap of dysregulated genes in these studies.
3.	It is surprising to me that there are no error bars for number of genes dysregulated atleast in one study across the 7 studies and so on.
4.	Statistical test for overlapping genes across the studies will be informative.
5.	The final results should be tested for how many interactions they hold true for atleast 3 studies.
6.	Line 186 about heterogeneity of disease should be reconsidered.
7.	Lines 224 -225, further references regarding osteoclasts role in RA pathology is essential.
8.	Graphical representation of osteoclast markers should be given across the studies compared to controls.
9.	Figure5 explain the meaning of size of nodes for pathways shown.
10.	Graphically represent the data for the gene involved in osteoclast differentiation among various studies to support the point and explain if there is any variation between them.
11.	Line 307 what is ODP network mean.
12.	Which figure have details about OPD network.  Showing core and shell network.
13.	Line 319 NFKB should be written NF-κB, just like line 332 and I appreciate that author’s have used kappa in line 332.
14.	Figure 8 title say activation of REL; however the network shown have many NF-κB family members, so update it accordingly.
15.	Why Rel was selected over other family members of NF-κB, line 348 suggests just overexpression. However, many GWAS studies also link Rel with RA. It will be interesting if authors can differentiate Rel specific pathways compare to other NF-κB family members.
16.	For figures 8 and 9 provide some weightage (score) to the nodes depending on the hits from the studies utilized to generate network.
17.	Suprisingly figure 9 doesn’t have any NF-κB association.


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

Input:
Title: EFFECTS OF RHEUMATOID ARTHRITIS ASSOCIATED TRANSCRIPTIONAL CHANGES ON OSTEOCLAST DIFFERENTIATION NETWORK IN THE SYNOVIUM
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: From my point of view the authors have satisfactorily discussed and executed the criticism and suggestions from the first review and I have no further comments. One technical point is that, still, I think that the abbreviation list for availability reasons should be included in the main manuscript if that is in accordance with the journals' instructions.


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

Input:
Title: EFFECTS OF RHEUMATOID ARTHRITIS ASSOCIATED TRANSCRIPTIONAL CHANGES ON OSTEOCLAST DIFFERENTIATION NETWORK IN THE SYNOVIUM
Review round: 2
Reviewer: 2

Output:
Basic reporting: The flow of the manuscript is improved in the revised version. English is clear and professional.
Experimental design: More experimental details are provided which help understand the methods.
Validity of the findings: No comments.
Additional comments: The legend of Figure 7 should only include up pathways/DEGs, and for Figure 8 should only have down. It's confusing to have both up and down in legends when one of them is not part of the figure.

Regarding the description of pathway enrichment, I am only concerned about the language used to describe the enrichment results (line 447-476). Why not simply say pathways enriched in up/down regulated genes? I feel that's a better description of results rather than up/down pathways, given the pathway output cannot be assessed. However, this is a minor point.


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

Input:
Title: EFFECTS OF RHEUMATOID ARTHRITIS ASSOCIATED TRANSCRIPTIONAL CHANGES ON OSTEOCLAST DIFFERENTIATION NETWORK IN THE SYNOVIUM
Review round: 2
Reviewer: 3

Output:
Basic reporting: Please see comments to author.
Experimental design: Please see comments to author.
Validity of the findings: Please see comments to author.
Additional comments: Shilpa et. al. have updated all the concerns raised by me during previous revision satisfactorily. Manuscript can be accepted for the PeerJ publication. I indeed like to make to point the authors have explained their points very well.


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

Input:
Title: MODULATING FACTORS OF THE ABUNDANCE AND DISTRIBUTION OF ACHELOUS SPINIMANUS (LATREILLE, 1819) (DECAPODA, PORTUNOIDEA), A FISHERY RESOURCE, IN SOUTHEASTERN BRAZIL
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript titled "Modulating factors on the abundance and distribution of Achelous spinimanus (Latreille, 1819): a fishery resource in the Brazilian Littoral Southeastern" analyzes the influence of abiotic variables on the distribution of the species in three bays of southeastern Brazil.
The work presents technical-scientific merit and is well elaborated, however, it presents some items that need adjustments, which are identified throughout the PDF and below.
Experimental design: The content discussed has already been analyzed and published by other authors, with notoriously original items, only a combination of some elements (as highlighted by the authors on lines 79-84).
There are two items that need to be clarified and / or better analyzed:
1. The authors use the identification of three different water bodies (Coastal Water, Tropical Water and South Atlantic Central Water) based on a 1987 publication. With so many changes in global temperature, has there been no values of these currents? What about the seasonal variation? Still, there is a temperature gap (from 18o to 20o) and salinity (36) that does not belong to any of these currents. The study of physical oceanography is more complex than a combination of temperature and salinity.
2. The influence of abiotic variables occurs together. It is known that it is impossible to quantify all the variables that influence animal life, but the variables that have been measured must be analyzed together and separate factors must be separated. Better explaining: if there are 18 distinct sites and 2 years, authors can not group all sites and evaluate by year, as each site is different and it is not allowed to group separate elements to be analyzed together. In the same way that it is not possible to affirm that the granulometry, by itself, determines the distribution of the animals, since there is also the influence of the water masses, the different bays, the depth, the organic matter, etc. That is, we suggest that analyzes be performed in which all variables are considered, and not isolate them.
Validity of the findings: The authors provided only the spreadsheet with abiotic data, and this made it impossible for us to evaluate some biological aspects. In this context, the main inconsistency of the work is not to insert data essential for the understanding of the distribution, which are the sizes, sexes and maturity of the copies. It is well known that for most Portunidae there is age and sexual segregation and different uses of Habitat. It is possible that the granulometry is directly associated with the juvenile or adult phase of the specimens; or not. The reader finishes the manuscript without having the knowledge of this information that is fundamental, since the subject approaches the factors that modulate the abundance and distribution.
Additional comments: In general, the main failure of the work is to analyze the variables independently, when there is notoriously a set of influences. For example, in Table 1, only the years were compared. But is there a difference between the sheltered areas of the waves and exposed areas? And between the bays? And between the months?
In the discussion, the authors make the same mistake, of analyzing each variable separately. How can it be said, for example, that temperature influences distribution if there are also other variables? So it is not the temperature, in fact, it is a set of factors. In this case, it is up to the authors to quantify the influence and importance of each variable. For this, we suggest a multiple analysis, a generalized linear model or a multivariate one so that the variables are analyzed in a weighted way.
Another item that was deficient in the work is that the authors affirm that the individuals were sexed, which is a fundamental aspect in the study of distribution. However, this information was not explored by location and time of year. We believe that this information is indispensable, as well as the classification of young people and adults.


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: MODULATING FACTORS OF THE ABUNDANCE AND DISTRIBUTION OF ACHELOUS SPINIMANUS (LATREILLE, 1819) (DECAPODA, PORTUNOIDEA), A FISHERY RESOURCE, IN SOUTHEASTERN BRAZIL
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors have sought assistance to improve language and grammar. However, there remains room for improvement, particularly with tense and word choice. The need for improvement to a level of professional English makes reading difficult in many places in the manuscript. For example, see lines 79-82. Also, what is a “naturally excluded” fishing area? What is meant by predatory fishing gear? Are not all fishing gear operated by predators (i.e., humans) using active (trawls) and passive (drift net, long lines) fishing gear?

The Introduction and background describe the context of this study.  The references are relevant, but  there is room for improvement as to how they are cited and referenced in the text. This issue relates more to proper English usage than a problem in not referencing in the text. For example, line 37 refers to “those authors” which refers to a previously cited paper. I suggest instead that the reference be repeated.

The overall structure conforms to Peer J standards. However, all of the cited references are in italics which is not correct. They should be Times New Roman, no italics.

The tables and figures are relevant, although more will be said later on what is presented. All are of good quality except Figure 5. The resolution of this figure needs improvement.

Raw data is provided. However, if the authors wish to reference it, then the data needs to be cited in the text.
Experimental design: Original research is presented that is within the scope of Peer J.

The research question is well defined, but the knowledge gap that it attempts to fill is not.  No justification is presented for repeating a study of environmental parameters affecting the spatiotemporal distribution of A. spinimanus. Previous studies with overlapping research goals and study areas are referenced, so the authors are aware of them ( for examples,  Lima et al 2014, Andrade et al. 2014). Within the lines of 85 – 90, a clear justification for repeating research and how this new effort attempts to fill knowledge gaps left by previous studies needs to be presented.

The description and justification of the sampling design needs improvement, particularly how sample locations were selected within bays. If Fig. 1 is an accurate representation of the three bays, then how the  20 m depth sample locations are justified as being located within their respective bays needs to be explained. They do not appear to be within any of the bays. The same can be said for the 15 m locations at MV and UBM.

The methods for species identification, temperature and salinity recording, and sediment analysis are described in sufficient detail.
Validity of the findings: The relationship between sediment composition and abundance of A. spinimanus confirms how sediment type influences the distribution of crabs previously shown by Lima et al. 2014. In addition, crabs are most abundant in “naturally excluded” area of UBA (this location needs to be named in the abstract). What is not addressed is how the RDS analysis is overwhelmingly influenced by the high abundance of crabs at UBA. Is not the sediment type relationship with crab abundance highly influenced by most crabs being caught in a naturally excluded fishing area? If there had been a bay that was not “naturally excluded” where similar numbers of crabs were found, the findings would be more convincing. In this respect, the discussion of stenotopic versus eutytopic is not convincing, especially since more than one environmental parameter is needed to define a species as such. More needs to be said to explain why a swimming crab is so influenced by sediment type.

The temperature data is pooled to make comparisons between years. Instead, since a rationale of the experimental design is to compare bays, the temperatures within each bay for each year should be shown and statistically compared. When reported in the results, the analysis should be in one paragraph instead of the serval now written between lines 166 – 183. The tables need to be better referenced, such as between lines 171 and 175 where not table is cited. Somewhere in the text is should be stated that the data passed or di not pass the Shapiro-Wilk and Levene’s Tests.

The potential interaction between Callinectes danae and A. spinimaus is interesting, but pure speculation and needs to be stated as such until someone studies the interactions between these two species.

The discussion of the influence of SASW is very interesting. What it needs is more information about the local oceanography of the coast and bays before any relationship between spatiotemporal distribution and season can be made. Otherwise, what is said between lines 227 and 232 is speculation and needs to be stated as such if included in a revised manuscript. The aspect of the bays (a measure currently named outfall) most certainly will influence the affect of SACW, although coastal currents will modulate that effect.

In conclusion, a reanalysis of temperature data and local oceanography will help support the explanations for the spatiotemporal distribution of Achelous spinimanus.  Differences and similarities between this study and previous ones showing sediment-animal relationship for A. spinimanus need to be clearly reported and discussed. Priority needs to be given to the finding that crabs were most abundant where they were protected from harvesting and how that has a  lesser or greater effect on distribution than sediment type. Until it is shown that the requirements of this crab species are narrow for a number of resources/parameters, any discussion about steno/eurytopic characterization should be very limited.
Additional comments: This is an interesting paper with good potential for publication. Personally, I think more might be said about how areas naturally protected from commercial harvesting are important for maintaining populations of this species. I also hope more can be added about local oceanography and SACW and how they might influence the distribution of Acheles spinimanus.


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: MODULATING FACTORS OF THE ABUNDANCE AND DISTRIBUTION OF ACHELOUS SPINIMANUS (LATREILLE, 1819) (DECAPODA, PORTUNOIDEA), A FISHERY RESOURCE, IN SOUTHEASTERN BRAZIL
Review round: 1
Reviewer: 3

Output:
Basic reporting: This paper is interesting and relevant to the field. The authors could make some minor improvements in the English, but overall it is very well written. I enjoyed reading the literature review.

However, I note that I am unable to comment on the impact of the findings because the authors did not include their raw code. I would be happy to continue the review once I see the R code used to compute the results outlined in this paper.
Experimental design: I am unable to comment on the impact of the findings because the authors did not include their raw R code.
Validity of the findings: I am unable to comment on the impact of the findings because the authors did not include their raw R code.
Additional comments: I would like to continue reviewing this paper, but I need to see the R code used to compute the results outlined here. If the authors could please include their .R file, I will continue my review.


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

Input:
Title: MODULATING FACTORS OF THE ABUNDANCE AND DISTRIBUTION OF ACHELOUS SPINIMANUS (LATREILLE, 1819) (DECAPODA, PORTUNOIDEA), A FISHERY RESOURCE, IN SOUTHEASTERN BRAZIL
Review round: 2
Reviewer: 1

Output:
Basic reporting: This revision shows a wonderful improvement in professional English. I commend the authors on their diligence and work. Now more clearly shown, there is sufficient background to set up the authors' hypotheses. The literature is amply supports the background, methods, and ideas discussed. Figures and tables all show professional structure and raw data are shared (at with reviewers -- not clear if they will be supplied as a supplement since not referenced as so anywhere in the text). I suggest that the authors cite their raw data as supplementary materials where that is appropriate in the text.

There are still a few places needing clarity and I have uploaded an annotated copy of the manuscript for the authors.
Experimental design: This revision meets all four criteria.
Validity of the findings: This revision meets all four criteria. The authors have made good progress revising their ideas and taking the reviewer suggestions. As a result, the ideas are more clearly understood.
Additional comments: This revision is greatly improved and addresses my concerns with the first draft. I have uploaded an annotated copy of this manuscript in the hope that my few suggestions will be seen as helpful and instructive.


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: MODULATING FACTORS OF THE ABUNDANCE AND DISTRIBUTION OF ACHELOUS SPINIMANUS (LATREILLE, 1819) (DECAPODA, PORTUNOIDEA), A FISHERY RESOURCE, IN SOUTHEASTERN BRAZIL
Review round: 2
Reviewer: 2

Output:
Basic reporting: I thank the authors for their timely resubmission of their manuscript materials. I have several comments in descending order of importance:

1. I strongly urge the authors to employ the assistance of a native English speaker to help modify the grammar and verbiage of the paper. The paper cannot be published until the English grammar is corrected.

2. I appreciate the excellent references and structure of the introduction to the paper.

3. The figures and tables are sufficient and pertinent to the main points of the paper. I thank the authors for sharing the raw R code used for their analyses, and I request that for the next submission, the R code and associated data tables are submitted as .R and .txt (or .csv or .xlsx) files, respectively.
Experimental design: The authors make clear the novelty of their research. I would like the authors to comment on the use of 20 year old data to build these models. I expect that there may have been significant ecosystem shifts in this period of time, and wonder how this could affect the findings.
Validity of the findings: The conclusions are outlined thoroughly in the discussion point, but again, I would like commentary about how these results may change if updated survey data were incorporated into the models. I would also like more commentary on the applicability of these findings to resource managers.
Additional comments: Thank you for making some revisions and including your code. Please see my comments above and within the document.


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: COULD RESISTANCE TO LACTATE ACCUMULATION CONTRIBUTE TO THE BETTER SWIMMING PERFORMANCE OF BRYCON AMAZONICUS WHEN COMPARED TO COLOSSOMA MACROPOMUM?
Review round: 1
Reviewer: 1

Output:
Basic reporting: Figures are clear and appropriate. English grammar requires work throughout. The text is generally clear but it requires substantial copy editing to meet the language requirements of the journal.
Experimental design: Although the experiment design is appropriate for the aim of the study, the general hypothesis of the paper is fundamentally flawed and the conclusions are not supported by the data collected. The authors argue that tolerance to white muscle lactate accumulation underlies the better swimming performance of matrincha compared to tambaqui but a substantial literature-base going back decades has shown that aerobic capacity, supported by cardiorespiratory function, is likely the most critical factor in determining athletic performance in fish (and most other vertebrates). The authors themselves discuss why a single measurement of lactate concentration in white muscle cannot be used to predict anaerobic capacity, since the simultaneous oxidation of lactate can also be upregulated.

The data collected are valid and the experiments appear to have been carried out rigorously and analyzed appropriately. The hypoxia experiment was not relevant to the study.
Validity of the findings: The data collected in the study provide a clear, straightforward answer to the question of why matrincha is a better swimmer:  Figure 2 shows that matrincha has an aerobic scope (the difference between minimum and maximum MO2) almost twice that of tambaqui. This illustrates that matrincha has a much greater cardiorespiratory capacity, likely a much greater capacity for oxidative phosphorylation, a much greater capacity to deliver O2 to working muscles and therefore avoid anaerobic metabolism, and finally a much greater capacity to oxidize any lactate produced in that working muscle. Unfortunately, the remainder of the data presented in the paper is not particularly helpful in answering the question posed.

The authors attempt to draw conclusions about plasticity of anaerobic capacity during swimming by measuring the Vmax of LDH, and not the actual flux of pyruvate to lactate. Substantial upregulation of maximum LDH activity requires the synthesis of new LDH protein, which is unlikely to occur during the energy limited conditions associated with a maximum swim performance test.
Additional comments: I would encourage the authors to re-frame the paper in a different way, perhaps focusing on the differences aerobic scope (recognizing that the maximum MO2 measurements may be slightly underestimated due to the logistics of the setup).

Line 50 – specify aerobic metabolic rate, since anaerobic metabolism will be occurring but you are only measuring O2 consumption.
Line 95-97 - clarify - does this mean that their swimming performance declined after exposure to hypoxia or that they were poor endurance swimmers in general?

Line 103-104 - Does environmental hypoxia increase white muscle [lactate] in these animals? Clarifying this point would help the reader to better understand the rationale for the current study. If hypoxia only increases plasma lactate, then that can act as an efficient fuel for swimming during normoxic exercise.

Line 115-117 - Lactate in white muscle is probably largely produced from on-board glycogen stores. Is swimming limited by glycogen content in these species?

Line 126-128 - but lactate is largely retained in the white muscle in fish, since they lack a Cori cycle. If lactate was released from the white muscle, it would be hugely concentrated in the blood since the white muscle makes up such a large proportion of total body mass in fish.

Line 136-138 - not increased cardiorespiratory capaciy - just cardiorespiratory capacity. Adding the 'increased' there implies that maximum cardiorespiratory function can be instantly increased by exercise.

Line 151-153 - This hypothesis seems to conflict with the background given that tambaqui will fatigue more quickly than matrincha.

Line 160-162 - phrasing is not accurate here. Contribution of NOx to facilitating cardiac scope would be more accurate.

Line 229-238 - There is no swimming post hypoxia test. The intro of the paper refers to that test often and makes it seem like that will be tested here.

In results text – if it is stated that something is ‘different’, make sure the statement is backed up by statistical testing and a p-value.

Line 270-272 -The MO2 data pretty clearly show that matrincha has a much greater aerobic scope than tambaqui, even though the maximum MO2 was not necessarily measured for either species. This alone largely explains why matrincha is a better swimmer.

Line 286-293 - The hypoxia experiment really doesn't add to this study. It is not directly relevant to the main question being asked and the data is not useful.

Line 300-302 - this implies that you confirmed the ability to accumulate lactate explains the better swimming ability in matrincha, which was not proven.

Line 308-310 – lactate cannot be both oxidized and stored - it is one or the other.

Line 322-328 - hydrodynamics were not addressed in this study so this conclusion is inappropriate.

Line 333-334 - It is confirmed by the MO2 data - swimming velocities are secondary. This interpretation is problematic in that it makes the assumption that higher metabolic rate allows higher swimming velocities but the entire premise of the paper was to test if lactate tolerance allowed higher swimming velocities.

Line 340- 345 – No, this is incorrect. It just has a lower maximum MO2 (lower aerobic scope). It is not as athletic. The metabolic rate data absolutely does explain the differences in swimming capacity. Tambaqui likely has both lower aerobic and anaerobic capacity (at least in the white muscle, which is not critical for hypoxia tolerance).

Line 347-359 - most of these parameters were not measured so it is not appropriate to spend this much time discussing them.

Line 365-367 - but NOx did continue to increase (although not statistically significantly) in the matrincha. It could contribute.

Line 375-376 - no, it most certainly is not. The LDH reaction does not produce ATP, it oxidizes NADH to NAD+ so that flux through glycolysis can continue in the absence of NADH oxidation by the ETC.


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: COULD RESISTANCE TO LACTATE ACCUMULATION CONTRIBUTE TO THE BETTER SWIMMING PERFORMANCE OF BRYCON AMAZONICUS WHEN COMPARED TO COLOSSOMA MACROPOMUM?
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment.
Experimental design: Regarding the experiment with fish exposure to the hypoxic condition, it is important that the authors justify the reason for having lowered the oxygen concentration of the chamber so quickly (in 30 min). Also justify why the fish had been exposed to hypoxia for only 1 hour.
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: COULD RESISTANCE TO LACTATE ACCUMULATION CONTRIBUTE TO THE BETTER SWIMMING PERFORMANCE OF BRYCON AMAZONICUS WHEN COMPARED TO COLOSSOMA MACROPOMUM?
Review round: 1
Reviewer: 3

Output:
Basic reporting: Some references listed at the end of the manuscript do not follow the journal standard. I suggest the authors review more carefully.
Experimental design: The experimental design is well described and detailed.
Validity of the findings: No comments
Additional comments: The manuscript “Does lactate or metabolic rate account for the better swimming performance of Brycon amazonicus when compared to Colossoma macropomum” investigating if matrinchã can keep swimming even with high lactate levels in muscle and analyzed the differences in aerobic and anaerobic metabolism between the fish species. The manuscript is constructed properly. The experiment is planned correctly, based on proper methods and does not arise any ethical or content-related reservations. Most of the results are presented carefully in very clear form. The presentation of the results in tables and figures can be improved. In this manuscript is required minor revision before its acceptance.
Comments
In the abstract, the name of the species must be separated.
I suggest putting keywords at the end of the abstract.
P5, L 4: Use superscript in identifying authors
P10, L 177: Change mg L-1 by mgL-1
P11, L 210: Describe the compound name MS-222
P12, L 235: Change ASR (aquatic surface respiration) by aquatic surface respiration (ASR)
The authors use many old references and many could be replaced.
P21, L513; P22, L537: The name of the journal is not in the rules.
P25: Describe in Figure 1 which means the x-axis


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: REGIONAL DIFFERENCES IN AN ESTABLISHED POPULATION OF INVASIVE INDO-PACIFIC LIONFISH (PTEROIS VOLITANS AND P. MILES) IN SOUTH FLORIDA
Review round: 1
Reviewer: 1

Output:
Basic reporting: This is a well written manuscript that adds depth to our understanding of the size of the population of lionfish in the invaded western Atlantic region. One of the main strengths of this manuscript is the scope, in terms of area surveyed, which is substantially larger than other studies of lionfish population sizes in the Atlantic that I am familiar with. However, the authors over emphasize the potential for depredation and harvesting explaining the lower densities of lionfish than expected without accounting for other variables that could be influencing the overall pattern they observe.
Experimental design: The survey design is appropriate for investigating the density of lionfish found in the regions survey and allows for the authors to compare these densities to the density of native fishes. Since the surveys go back to 1979 (Line 80) the authors could compare densities of native species before and after the lionfish invasion to see if there are differences in the native community coincident with the invasion of the lionfish. While an analysis of all fishes may be beyond the scope of this manuscript, specifically looking at changes in the competitor/predator densities could support the discussion of the role of competitors/predators in regulating the densities of lionfish.
Validity of the findings: The authors primarily focus on the likely influence of competitors/predators coupled with human exploitation as the primary explanation for the observed density of lionfish being lower than expected. However, there are other possible reasons that should be addressed either to show that the expectation from those explanations differs from what is observed or to show that they may be other explanations which need further investigation. For example, habitat may play a role in the patterns observed. The authors state that there are differences in habitat types among all three surveyed locations as well as within locations (Lines 98-118). From my understanding, these differences in habitat are pooled together to determine regional densities of lionfish (Lines 142-144). However, when comparing among regions and to other literature there doesn’t appear to be an analysis of differences in densities observed based on habitat type. It may be for example that the densities of lionfish in their “preferred” habitat in the survey area is similar to elsewhere in the Caribbean and the literature reviewed consistently surveys more preferable habitat without incorporating the less desirable habitat thus accounting for the differences. An analysis of the lionfish density as it relates to the surveyed habitat type would be ideal to see if A) there are differences among habitats which may explain some of the pattern observed within this survey and B) help in improving the ability to compare this study with other literature.

In lines 295-302 the authors posit that there may still be an effect of lionfish on native fish densities despite the relatively low densities of lionfish. The authors should consider utilizing the model developed by Green et al. (2014) in order to probabilistically determine if there is likely to be an effect of lionfish given the current health of the native fish populations and current lionfish densities. This would be helpful to guide future research and would provide an interesting test case for the model Green et al. develop. Further, if the authors choose to perform the analysis I mentioned above this model could be incorporated into that analysis to see the potential for local effects of lionfish beyond simply the regional scale, though this may well be beyond the scope of this manuscript.
Green SJ., Dulvy NK., Brooks ALM., Akins JL., Cooper AB., Miller S., Côté IM. 2014. Linking removal targets to the ecological effects of invaders: a predictive model and field test. Ecological Applications 24:1311–1322. DOI: 10.1890/13-0979.1.
Additional comments: This is an excellent manuscript documenting the invasion of lionfish into south Florida. The discussion focuses primarily on the potential role of humans and competitors/predators on maintenance of the low densities of lionfish observed. This should be explored further to support the supposition that these are the prime factor in controlling lionfish density or other factors should also be explored as depredation/exploitation is only one of a myriad of potential causes for the lower densities, habitat being the most obvious example I can think of.


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: REGIONAL DIFFERENCES IN AN ESTABLISHED POPULATION OF INVASIVE INDO-PACIFIC LIONFISH (PTEROIS VOLITANS AND P. MILES) IN SOUTH FLORIDA
Review round: 1
Reviewer: 2

Output:
Basic reporting: See below
Experimental design: See below
Validity of the findings: See below
Additional comments: Review of Bryant et al

In this paper, the authors examine 9 years of lionfish data from the Florida Reef Tract, beginning in 2009 when the invasion was first detected in the Florida Keys. The authors use an existing monitoring dataset to examine differences across regions. Interestingly, they note that the Dry Tortugas, which is more remote and more protected from fishing, and therefore has higher abundances of predatory fish, has lower abundance of lionfish. This encouraging result suggests that native predators may be able to at least partly control the lionfish invasion. While other work has suggested this may be true, this is the most compelling dataset to date since it covers a large area. I believe this manuscript will make a useful contribution to our understanding of the lionfish invasion.

That said, there are a few issues that require attention.

First, the sampling methodology employed in this study likely underestimates the actual abundance of lionfish, since lionfish can be cryptic and this method targets conspicuous reef fishes. The methods employed in this study are not lionfish specific, and therefore likely underestimate the actual abundance, particularly relative to lionfish-specific surveys used elsewhere. Therefore, the comparisons between Florida and other locations may not be valid, and the burden of proof is on the authors to demonstrate that their data are comparable. For example, REEF has conducted lionfish-specific surveys in the area; how well do those estimates match the ones presented here?

That said, data describing relative differences within part of the Florida Reef Tract where these methods are used consistently is useful, and I strongly encourage the authors to focus their framing and discussion on comparisons within their dataset. It is ok to mention other locations, I think this should occur only in the discussion and should be concurrent with a discussion of these methodological issues, emphasizing the uncertainty of such comparisons to elsewhere in the Caribbean or Indo-Pacific.

Second, the authors should consider other factors that may impact lionfish abundance, such as habitat and area. For example, the Dry Tortugas is fairly isolated oceanographically, such that there may be significant self-recruitment. Low abundance of lionfish there may provide fewer recruits than elsewhere. The Florida Keys may receive recruitment from the Keys themselves and from the Dry Tortugas. In addition, Lionfish were first detected in the SE FL region in 1985, so they have been established there much longer than FK or DT, and may also receive recruitment from downstream locations in the Keys and Dry Tortugas.

Habitat may also impact lionfish abundance; the complete patch-reef forereef structure in the Keys may serve as better lionfish habitat than many areas in the Dry Tortugas, so some examination of habitat-specific densities would be helpful.

While the potential predator control effect is compelling, the authors need to acknowledge additional factors that may drive the patterns they observe in these data from a large-scale survey program.

The scholarship also needs improvement. There are many places where citation of related work is needed; in some cases, citations need to be broader than they are, and other cases, entire statements require a citation or a few. I suggest a critical read through the MS, and that the authors include additional references where appropriate.

Specific comments:

L75: I like this approach; THIS should be the focus of the paper, not the comparisons to other Caribbean/Indo-Pacific locations
L126-152: These methods are described in detail in Smith et al 2011; these methods could be significantly condensed. At the very least, the formulae and detailed descriptions could go in supplementary materials.
L179: Citation needed (an example; there are several other locations where the scholarship could be strengthened
L190-192: Again, I am not convinced that these comparisons are appropriate, and despite this caveat, the authors make these comparisons explicit in Fig 3 (which I believe should be removed)
L201-202: The sharp decline suggests sampling error to me, and possibly detection error by new divers since lionfish are difficult to detect. How much were observers trained to search for lionfish from year to year? If it is real, this decline is very intriguing, but again, the authors need to convince me that it is real.
L213-215: Once again, I am not convinced comparisons to other regions are valid, and in any case, there are no statistics to support a claim that densities are ‘lower.’ The authors need to convince me that the comparisons are valid in the first place and provide some way of evaluating differences. The simplest solution would be to remove these comparisons
L219-221: Again, how different were these survey methods? Were methods in Kulbicki 2012 lionfish specific? If so, these densities are almost certainly not comparable
L238-240: Again, I'm not sure I believe these comparisons, since methods differ.
L240-243: I don't think the data support this interpretation at all.
L247-249: Citations needed.

Figures:
Fig 3: I would remove figure 3 for the reasons described above.

Figs 4 and 5: Why not use biomass for predatory species? Biomass integrates size and abundance, and might be a better proxy for potential lionfish predators than numerical density.


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: REGIONAL DIFFERENCES IN AN ESTABLISHED POPULATION OF INVASIVE INDO-PACIFIC LIONFISH (PTEROIS VOLITANS AND P. MILES) IN SOUTH FLORIDA
Review round: 2
Reviewer: 1

Output:
Basic reporting: In this manuscript, the authors present important data regarding the population density of lionfish in various regions of Florida. The authors have done a good job addressing my previous comments and concerns. Below are some fairly minor changes I feel would improve the manuscript and one addition needed in the methods.
Experimental design: No Comment
Validity of the findings: L204-216: You don't mention in the methods how the differences between strata within regions were statistically tested. If you used the same method as you did for statistically analyzing differences between regions (95%CI t-test) then that should be mentioned in the methods. If not then the method that was used should be mentioned.
Additional comments: Minor Comments:

L142: In this equation (and the equation in L151) I believe the subscript 'st' is to denote that the density is for the region. However, previously different subscripts had been used that did not include a region subscript. I would find it clearer if instead of introducing new and undefined subscripts you simply rephrase L132 to say something like "the mean density for each PSU (i) in stratum (h) in region (r)" and then alter the formulas to represent this as the labeling convention to maintain consistency across all the various equations.

L142: Are there meant to be 3 horizontal lines over the "Dst" in this equation since it is the third mean (SSU to PSU then PSU to Strata then Strata to Region)?

L145 &147: The equations on these two lines appear to be identical and from the context of the methods I believe they are meant to be different (specifically the subscripts).

L217-220: It would be helpful to report the total number of species as well as the ranking of lionfish. For all I know reading this section there are a total of 134 species in the Dry Tortugas, 95 species in the Florida Keys and 78 species in southeast Florida, this would be interesting of course but would be a far different message than what I believe this paragraph is coveying (i.e. that lionfish are fairly common but not the dominant species numerically). The same holds for the number of piscivores present.

L232: Change "have appeared" to "appear"

L233-236: Because you removed the figure comparing lionfish densities in this study to previous studies it may be a good idea to include some of the values presented for the native and invaded range in the text since you do mention the comparison as something of interest here.

L238: Change "depends" to "depend"

L264-265: Is the diet overlap between small piscivorous fishes and lionfish similar at all life stages (of the lionfish) or at particular life stages? If it is specifically similar to the diet of juvenile lionfish then that would be worth mentioning especially given the apparent transition from crustaceans to fishes as lionfish age (Morris and Akins 2009, Dahl and Patterson 2014).

Figure 3 Legend: One of the abbreviations is "CONT_MR" that is said to stand for "continuous low relief". In later abbreviations, low relief strata are termed "_LR". Is this meant to be abbreviated as "CONT_LR" or is it a "continuous medium relief site"?

Figure 3: This figure does not aesthetically match the other figures (e.g. background colour). I would suggest changing this so all the figures are similar aesthetically.


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: PRODUCTION OF EXOPOLYSACCHARIDE BY STRAINS OF LACTOBACILLUS PLANTARUM YO175 AND OF101 ISOLATED FROM TRADITIONAL FERMENTED CEREAL BEVERAGE
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1. Lines 95-96, to the affirmation “Few works have been reported on EPS-producing LAB strains from cereals-based fermented food”, is there any reference?

2. The relevance of antioxidant activity of EPSs should be succinctly added to Introduction section, since this activity was tested in EPSs of present study. It can be mentioned that antioxidant activity of natural polysaccharides, including those of microbial EPSs, has gained great importance in recent decades since they are nontoxic antioxidants.

3. Figure 4, the contour plots which correspond to response surface three-dimensional plots present low resolution, which difficult the visualization. Please, improve their resolution.
Experimental design: 1.	The screening of optimal conditions for EPS production by isolated strains is not performed in food matrix, but in modified MRS broth. Thus, the optimal conditions and EPS yield found in MRS may be not reflected in food matrices. Therefore, the use of MRS broth in this study to evaluate the optimization conditions of EPS production by isolated LAB strains should be justified in Material and Methods section.

2.	Line 119, the previous step performed to obtain the pellets mentioned in “The resulting pellets obtained were mixed with ultrapure water” should be described. Citations should not be used as a substitute for providing the details of a procedure.

3.	Lines 133-134, please report your methods with sufficient detail so readers do not need to refer to other papers to understand how procedures were performed.

4.	Lines 138-139, what column and run conditions of HPLC were employed? Were they the same used for molecular mass determination of EPSs? It need be specified.

5.	Lines 139-140, please report your methods with sufficient detail so readers do not need to refer to other papers to understand how procedures were performed.

6.	Lines 155-158. Describe, even if succinctly, the methods employed so readers do not need to refer to other papers to understand how procedures were performed.
Validity of the findings: 1.	Lines 145-150, the preliminary screening of cultivation condition and media composition for EPS production was performed to determine the significant factors for this production. However, what was the statistical analysis used to determine which factors are significant for EPS production? It was ANOVA? What significance level was considered for this statistical analysis? This information should be added in Statistical Analysis section.

2.	Figure 6. It would be interesting to perform a statistical analysis comparing the antioxidant activities of EPSs studied with the control (ascorbic acid), well as to compare the antioxidant activities of EPSs between the different strains studied. The statistical analysis employed should be described in Statistical Analysis section. The statistical results should be added to graphs in Figure 6. The statistical analysis is an essential tool to determine if the differences found between the values are significant.

3.	Table 2B, highly significant lack of fit (p-value = 0.0005) indicates that a new model is needed. The employed quadratic model for production of exopolysaccharide in Lactobacillus plantarum OF101 should not be complex enough to fit the data (important terms from the model such as interactions or quadratic terms should not have been included). From analysis of data, it seems that large residuals result from fitting the model should not has been the cause of lack of fit. I suggest evaluating other model that cans suitability to fit the data.

4.	Figure 3, it is essential that be performed a statistical analysis with the data of Figure 3. It seems that there was no significant difference for EPS yield, for example, between the sucrose and lactose conditions, well as between the conditions of yeast extract and peptone, even so sucrose and yeast extract were reported by authors as optimal conditions for EPS yield when compared to others. The statistical analysis employed should be described in Statistical Analysis section. The statistical results should be added to graphs in Figure 3. The statistical analysis is an essential tool to determine if the differences found between the values are significant.
Additional comments: The manuscript titled, "Production of exopolysaccharide by strains of Lactobacillus plantarum YO175 and OF101 isolated from traditional fermented cereal beverage", proposed to optimize the production conditions of EPS by Lactobacillus plantarum strains isolated from ogi, a traditional fermented cereal beverage, followed by measurement of their antioxidant activities.

The paper was well organized, writter in good English and with a clear introduction. It was clearly stated how research fills an identified knowledge gap. The authors did a good job in results and discussion by clearly presenting results in tables and figures and comparing results with those described in literature. The weaknesses were the statistical analysis and the detailed poorly material and method section.

The reviewer recommends acceptance with major revisions.

1.	Line 70, detail the GRAS term (Generally Recognized as Safe). The first mention in a text need be detailed.

2.	Line 81, unclear sentence. Change “They form” by “It forms” if is referring to the ogi.

3.	Line 86, typing error. Isolate the term Lactococcus of lactis term.

4.	Lines 95-96, the statement is not very clear. I suggest to rewritter as follows: “Few works have been reported on EPS production ability by LAB strains isolated from cereals-based fermented food.”

5.	Line 151 should be deleted. Lines 152-153 should be moved for the Statistical Analysis section.

6.	Line 171, the authors report the figure S1 which is in Supplementary Material as Figure S2.

7.	Line 176, the authors report the figure S2 which is in Supplementary Material as Figure S1.

8.	In Discussion section, it is relevant compare the EPS yield found with data reported in literature. The results reported here were higher, lower or similar those reported in literature?


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: PRODUCTION OF EXOPOLYSACCHARIDE BY STRAINS OF LACTOBACILLUS PLANTARUM YO175 AND OF101 ISOLATED FROM TRADITIONAL FERMENTED CEREAL BEVERAGE
Review round: 1
Reviewer: 2

Output:
Basic reporting: L71-75:One of the author's purpose is to evaluate the in vitro antioxidant activity of the EPS from L. plantarum strains. However, no background or rationale about the antioxidant activity of the EPS was done in the introduction section. I suggest the authors to describe here studies demonstrating antioxidant activity of EPS from lactobacillus.

L102: Change “characterize” to “evaluate”.
Experimental design: No comment.
Validity of the findings: L159: There are lacking information about the statistical analysis. Please describe all statistical tests performed in the manuscript.

L227. It is more interesting the authors show their results based on statistical tests instead of saying "the scavenging effects of the EPS increases as the concentration increased". Were the antioxidant capacity increases statistical significant? Please provide statistical sinificance information for all antioxidant analysis. Furthermore, I suggest include a correlation analysis in order to show the relationship between antioxidant activity and EPS concentration.

L282-285: The discussion on the antioxidant activity results should be improved... The authors can do it after making the statistical analysis as I have suggested above.

L291-292: Since no statistical analysis was done for the antioxidant analysis, the authors can´t state in their conclusion that the EPS produced by the two L. plantarum strains have significant antioxidant potentials.
Additional comments: The present study was developed with the purpose of improving the production of EPS from L. plantarum strains and to evaluate the antioxidant activity in vitro. Although the present work has a great scientific contribution, there are some points that need to be clarified in order to improve 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: PRODUCTION OF EXOPOLYSACCHARIDE BY STRAINS OF LACTOBACILLUS PLANTARUM YO175 AND OF101 ISOLATED FROM TRADITIONAL FERMENTED CEREAL BEVERAGE
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: 1.	Figure 3. The description of standard deviation among replicates not indicates if there is significant difference among the different treatments. The standard deviation measured the amount of variation or dispersion of set of data values within of a same treatment. The authors reported sucrose and yeast extract as optimal conditions for EPS yield when compared to others conditions. The question is: the differences in EPS yields observed for a same strain in different carbon sources (glucose, sucrose, lactose and galactose) are significant? The difference in EPS yields for a same carbon source (medium with glucose, for example) for different strains is significant? The same questions should be done for sucrose concentration, organic nitrogen, inorganic nitrogen, temperature, cultivation time, and pH. For the conjunct of data of EACH graph, I suggest to perform ANOVA two-way with significance level of 0.05. The statistics differences should be represented by symbols in each graph of Figure 3. In legend of figure should be briefly added information about the statistical analysis employed and description of symbols used.

2.	Figure 6. The description of standard deviation among replicates not indicates if there is significant difference among the different treatments. The standard deviation measured the amount of variation or dispersion of set of data values within of a same treatment. For example, the authors reported that the reducing power of the ascorbic acid, EPS-YO175 and EPS-OF101 at 4 mg/mL concentration are (0.91˃0.41 ˃ 0.34). The question is: the reducing power of ascorbic acid, in this concentration, is significantly higher than of EPSs obtained from of different strains? In this concentration, the reducing power of EPS-YO175 is significantly higher than of EPS-OF101? Similar questions should be done for each concentration level of reductor agents. For the conjunct of data of EACH graph, I suggest to perform ANOVA two-way with significance level of 0.05. The statistics differences should be represented by symbols in each graph of Figure 6. In legend of figure should be briefly added information about the statistical analysis employed and description of symbols used.
Additional comments: 1.	In Supplementary Material, in legend "Dry EPS produced on MRS-Sucrose modified media", change the term Fig S2 by term Fig S1 in order to be in accordance with the description performed in manuscript.
2.	In Supplementary Material, in legend "TLC plate showing the monosaccharide composition of the EPS samples", change the term Fig S1 by Fig S2 in order to be in accordance with the description performed in manuscript.
3.	Lines 177-179, please, correct the legend referent to formula of the DPPH radical (%) scavenging activity: Ab = Absorbance of blank and Ac = Absorbance of control
4.	Lines 336-337, your results should be discussed with those reported in literature.


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: PRODUCTION OF EXOPOLYSACCHARIDE BY STRAINS OF LACTOBACILLUS PLANTARUM YO175 AND OF101 ISOLATED FROM TRADITIONAL FERMENTED CEREAL BEVERAGE
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: The authors have addressed all my comments in an adequate manner. I have no further comments.


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

Input:
Title: ALCOHOL CONSUMPTION AND SLEEP DEPRIVATION AMONG GHANAIAN ADULTS: GHANA DEMOGRAPHIC AND HEALTH SURVEY
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1.  The introduction  needs  more  detail.  I  suggest  you  develop  lines  243-257  further  for  the introduction  by  reviewing  sleep  and  alcohol  studies  conducted  in  Sub  Saharan  Africa countries.

2.  Line  72-80:  You  provide  information  from  a  wide  range  of contexts.  I  suggest  that you extrapolate  on the effect  and costs  of  alcohol related  sleep disorders in Ghana  as well.

3.  There  appears  to  be  a  contradiction  in  line  95-96  compared  with  your  description  of sleep studies in these  regions in lines 243-252

4.  Line  95-96,  282-  284.  This  assertion  might  be  accurate  for  Ghana  but  not  ‘in  an  African setting’.  Several  studies  have  explored  alcohol  and  sleep  in  sub  Saharan  Africa  for example  in  Nigeria.  Consider  conducting  a  literature  review  beyond  Ghana,  or  restrict the argument in this section to Ghana.

5.  Consider  your use  of acronyms by  spelling  them out  at first use.

6.  The English  language  should  be  improved.  Consider  rephrasing  lines,  30,  72,  112,  172, 151,  200,  259,  261,  267, 294, 295.

7. Consider making available a link to the public DHS data.
Experimental design: 'No comment'
Validity of the findings: Limit  your  discussion  in  line  270-272,  to  those  supported  by  the  results.  Provide  a  link  to  the original  DHS data.
Additional comments: This  is  a  preliminary  study  in  the  right  direction.  I  commend  the  authors  for  identifying  and acknowledging  the  various limitations in  the study  and  providing  direction  for  further studies.


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

Input:
Title: ALCOHOL CONSUMPTION AND SLEEP DEPRIVATION AMONG GHANAIAN ADULTS: GHANA DEMOGRAPHIC AND HEALTH SURVEY
Review round: 1
Reviewer: 2

Output:
Basic reporting: The English language should be improved to ensure that an
international audience can clearly understand your text.
Some examples where the language could be improved
include the abstract :In this study investigated whether current
alcohol consumption has any influence on sleeping hours among adult men and women in
Ghana" – the current phrasing makes
comprehension difficult.

Some citations were wrongly attributed, e.g. According to World Health
94 Organization estimates, Sub Saharan Africa (SSA) ranks among the regions with highest per capita consumption of alcohol in the world(Onwuka et al., 2016).
It would make sense to cite the original WHO document where this information can be found.

Also reference no 1. was wrongly stated. My PUBMED Search revealed that the correct citation is: Barrett PR, Horne JA, Reyner LA.Alcohol continues to affect sleepiness related driving impairment, when breath alcohol levels have fallen to near-zero.Hum Psychopharmacol. 2004 Aug;19(6):421-3.

Also reference no. 2 is supposed to be:

 Wasielewski JA and Holloway, FA. Alcohol’s Interactions With Circadian Rhythms: A Focus on Body Temperature. Bethesda, MD, United States: National Institute of Alcohol Abuse and Alcoholism.
Experimental design: Original primary research within Aims and Scope of the journal.
Research question well defined, relevant & meaningful. It is stated how research fills an identified knowledge gap

The research question is not well defined. Please state the research question.
Validity of the findings: Data is robust, statistically sound, & controlled.
Additional comments: Your references do not meet the journal format. Also some of your references lack basic information even when they have been updated in PUBMED. Please go through all of your references and format very well. Your manuscript would required the assistance of a native English speaker to improve the language structure.


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

Input:
Title: EFFECTS OF WINE-CAP STROPHARIA CULTIVATION ON SOIL NUTRIENTS AND BACTERIAL COMMUNITIES IN FORESTLANDS OF NORTHERN CHINA
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Gong et al. described different regimes of wine-cap Stropharia cultivation on the soil properties and microbial community. They found the wine-cap Stropharia cultivation improved soil organic matter and nutrient availability. No significant difference of microbial diversity was observed but specific bacteria groups increased with wine-cap Stropharia cultivation. It is sounds good topic to culture mushroom in the forestland. However, the MS writing should be greatly improved before it is accepted. First, the introduction section is very poor to state the scientific importance of this study. The statement was more focused on techonoloy question. Second, the description of the materials and methods section is not very clear. What size of the forestland experiment site? The mother materials of each plots is the same? Third, as we known, in the process of mushroom cultivation, a lot of raw organic materials such as straw, wood sawdust were input to the cultivation bed. How to distinguish the effect of the raw organic materials addition from the mushroom cultivation? Moreover, the soil samples collection was clear in this MS. Do the author remove all the raw organic materials from the samples? If not consider this question, the conclusion of the MS should be revised. They found the organic matter determined the soil microbial community. Finally, some interpretation should be clear. For example, the subgoup_6 is not clear enough. Please check the whole MS. The significance of this MS should be highlighted. I can't find any new knowledge of this MS.


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

Input:
Title: EFFECTS OF WINE-CAP STROPHARIA CULTIVATION ON SOIL NUTRIENTS AND BACTERIAL COMMUNITIES IN FORESTLANDS OF NORTHERN CHINA
Review round: 1
Reviewer: 2

Output:
Basic reporting: Generally the manuscript is clear, however, there are some grammatical errors. I have highlighted a few, but it would take about an hour for a native speaker to check this.
Experimental design: Please see my attached review report.
Validity of the findings: please see my attached review report.
Additional comments: please see my attached review report.


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

Input:
Title: EFFECTS OF WINE-CAP STROPHARIA CULTIVATION ON SOIL NUTRIENTS AND BACTERIAL COMMUNITIES IN FORESTLANDS OF NORTHERN CHINA
Review round: 1
Reviewer: 3

Output:
Basic reporting: The structure and English sentences are need to be improved for clear understanding of whole contents of the manuscripts.
Authors addressed the mycosphere (or hyphosphere) effect on the bacterial communities in the forest soil. In introduction, however, cultivation effects (e.g. SMC or cultivating regimes) are only considered. Introduction of possible effect of mushroom hyphae on the bacteria is need to be added.
Experimental design: Experimental design was partially well designed, while some regimes are omitted in the design. For examples, why Y100/Y110/Y111 were not included in the design? If author think it is not needed in this analysis, please provide the reason for exclusion of some regimes.

It is not required, but I feel the lack of analysis. Although differences between all regimes were noted in post hoc analysis, authors mainly focused on difference between control and cultivation plot. I think this is waste of the other results including different effects depend on cultivating regimes. If it is possible to considering the pattern of regime effect, it will improve the quality of the analysis and provide better insights. However, I understand if it is not possible to conduct the additional analysis.
Validity of the findings: The topic is interesting, the most conclusions are based on the evidence provided in the results. However, some conclusion is lack of evidence.
1) “Given the severe nitrogen loss and the low quantity of NIB in Y001, an appropriate application of nitrogen fertilizer is suggested when S. rugosoannulata is first cultivated in forestland”
 - Given the results from Y010 or Y011, the nitrogen contents in forest soil were recovered to it of control plot in second year cultivation or non-cultivation. Why additional nitrogen fertilizer is need to apply?

2) “The highest content of soil nutrients in Y101 suggested that overyear cultivation might represent the best regime.”
 - Authors mentioned “best regime”, but I cannot understand the meaning of “best”. Best for who? Forest ecosystem or farmer? If it is better for farmer, what do you think the effect of increased nitrogen contents on the forest ecosystem?
Additional comments: The manuscript describes the effect of Stropharia rugosoannulata cultivation on the soil properties and bacterial communities in various regimes. Cultivation of S. rugosoannulata increased organic matters and available phosphorus in forestlands soil. In addition, changed of bacterial communities depend on the cultivation regimes was detected using high-throughput sequencing technology. Given the high interests of the wine cap mushroom in China, this study is important to understand the effect of mushroom cultivation on the forest soil ecosystem, and suggest the possibility of relevant cultivation strategy for reduce its negative impacts. However, several points in the manuscript are need to improve for support author’s arguments.

# Major comments
1. Many part of analysis methods or results are lack of detail information or misapplied. This is severe problem, and should be fixed appropriately. Details were noted on the below.

2. Authors used “mycosphere” concept, while it can be inappropriate. Of course, mycosphere is sometime used broad meaning that the environments influenced by the fungus or mushroom. However, mycosphere is more largely used as the soil environments under the fruiting body (mushroom). Thus, Stropharia cultivation plot is not mycosphere, but can be called different concept such as hyphosphere. The previous studies for hyphosphere, shiro of T. matsutake, or ectomycorrhizal mat are agree with the results from this study. Therefore, I recommend that change the mycosphere concept to hyphosphere or add the studies for hyphosphere effect on the bacterial additionally.

3. I suggests additional analysis to detect pattern of bacterial communities. Bacterial communities were separated too much depend on cultivation regime. It can be true, but I worried the analysis miss real pattern of nature. Authors used PCA, but it can be artificial patterns can be generated if OTU matrix were not transformed well. Distance-based ordination analysis (e.g. PCoA or NMDS) may be other options. In addition, weighted Unifrac-based analysis can elucidate different pattern of bacterial communities that was missed by non-phylogenetic distance based analysis.

4. What do you think which factor is more influential on the soil nutrients and bacterial communities between effect from SMC and mushroom hyphae?

# Minor comments
Line 1: In title, “bacterial properties” is inappropriate in this context. I think “bacterial communities” is better.
L32: Is AP meaning available potassium or available phosphorus?
L36: Subgroup_6 is lacking information. Where this taxa is belonging?
L50: What is the meaning of “rich raw materials”, specifically for what kind of material?
L57: Change “N” to “nitrogen”, and provide citation.
L74: How incineration or discard reduce pollution?
L95: What is the meaning of “excellent”?
L118: Change “soil measurements” to “measurements of soil properties”.
L122: Where is the results from the isolation?
L125-126: Authors can change “the Shandong Provincial Key Laboratory of Soil Erosion and Ecological Restoration, Tai’an, Shandong, P. R. China” to “the Shandong Provincial Key Laboratory of Soil Erosion and Ecological Restoration (Tai’an, Shandong, China)”.
L130: N means nitrogen?
L141-143: Add the appropriate reference of the primers.
L144: Add “ribosomal”.
L148: Add “final”.
L159: Change “Bioinformatics” to “Bioinformatic”.
L163: Change “Qiime” to “QIIME”. What option did you use for quality filtering?
L164-165: What kind of the reference database was used? Gold databased from Broad Microbiome Utilities or SILVA? Please provide the citation.
L169: Change “annotation” to “taxonomic assignment”, and “species annotation” to “species assignment”.
L170: What the meaning of Mothur method? Naïve Bayes classifier?
L171: Change “SSUrRNA” to “SSU rRNA”. The citation, Quast et al. 2013, is not present in the reference list.
L172: The purpose of sequence alignment is construction of distance matrix or phylogenetic tree, not for detecting community difference. What kind of method did you use?
L174: Change “normalized” to “rarified”.
L178: QIIME
L179: Did you transform the OTU matrix before conducting PCA?
L180: please give the citation.
L181: Is the citation, Sheik et al. 2012, relevant?
L187: What kind of multiple test correction method was used?
L200-201: please match the order of soil properties to the order in Table 2.
L205: please match the order of plot groups to the order in Table 2.
L245: VIF analysis is for identifying the multicollinearity in the soil properties, but is not for detecting contribution of soil properties on the bacterial communities. Author may be confused on the VIF and CCA analysis.
L294-306: As mentioned above, change or add add hyphosphere concept
L311:  What is meaning of NIB?
L314: What is the evidence that show OM content was the primary factor? CCA showed most of soil factors significantly influence on the bacterial communities.
Table 2, L3: Change “AMOVA” to “ANOVA”.
Figure 1: please give more information on the subgroup_6. I don’t think that “unidentified Acidobacteria” is inappropriate taxonomic group because it is complexity of various taxa that is difficult to identify based on sequence database, thus there is no taxonomical or ecological meanings.


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

Input:
Title: EFFECTS OF WINE-CAP STROPHARIA CULTIVATION ON SOIL NUTRIENTS AND BACTERIAL COMMUNITIES IN FORESTLANDS OF NORTHERN CHINA
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: This version of the MS has been improved according to the suggestions.


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

Input:
Title: EFFECTS OF WINE-CAP STROPHARIA CULTIVATION ON SOIL NUTRIENTS AND BACTERIAL COMMUNITIES IN FORESTLANDS OF NORTHERN CHINA
Review round: 2
Reviewer: 2

Output:
Basic reporting: I cannot fully understand the meaning of “best regime for soil” in the manuscript, and it might be due to lack of connection between background information and results from this study because the information is scattered in the manuscript. Based on Introduction and author’s responses, it seems that soil improvement is needed in China and mushroom cultivation in forestland may help to increase soil nutrients. If my understanding is right, please clarify the rationale of this study based on the connection between soil condition in China and the possible effect of Stropharia cultivation on soil nutrient, and please specify the criterion for “best regime” (e.g. increasing OM content in soil) in objectives parts.
Experimental design: Although authors added the details, many parts are need to add more information and analysis.

L156-158: Primer 515F and 806R were not developed by Zhang et al., (2014). Please give appropriate citation.
L186-188: Please give a taxonomic assignment method. Mothur is not the method. Based on the reference (Wang et al., 2007), authors might use Naïve bayesian classifier.
L188-189: Did you make a phylogenetic tree? If you made, please give the information.
L204-205: What kind of multiple testing correction method was used for Tukey’s test? Bonferroni or FDR of Benjamini-Hochberg?
L209-211, 265-267: AMOVA based on sequence alignment (or matrix) is not enough to test community differences (beta-diversity) because it only consider sequence difference while difference of OTUs composition is missing. Thus, I suggest add MANOVA-based test (e.g. ADONIS, PERMANNOVA, ANOSIM) for comparing bacterial community in each regimes.
L213: What kind of transformation method was used for PCA? Hellinger?
Validity of the findings: None
Additional comments: The manuscript has been revised well, while some parts are need to be changed more.

# Major comments
1. Authors discussed about N loss in second paragraph. However, TP loss was also significant. Please discuss about P loss as did for N loss.

# Minor comments
Line 40: The meaning of “beneficial to the forest soil” is ambiguous. Please, specify it (e.g. beneficial to nutrient condition in the forest soil).
L69: Change “soil” to “soil nutrient”.
L75: Change “pollution” to “air pollution”.
L83-84: Sentence is not complete.
L98: Change “20m × 150m” to “20 m × 150 m”.
L194-200: This part is overlapped to L213-L219. Please merge it.
L223: Remove “and” between pH and OM.
L238: These phyla were not significantly different between “all cultivation regime” and non-cultivation regime. Thus, change “cultivation” to “one of cultivation”.
L249: “diversity” is need to be in non-italic.
L273-L275: Correlation between OM and the number of OTUs or Shannon’s diversity is not mean that OM is main driver on bacterial “community”. It is the result for relationship between OM and alpha diversity. Of course, it seems that OM influence on both of diversity and community structure, but authors need to write the sentence appropriately.
L321: Change “fingi” to “fungi”.
L342: “best regime”. Same above.
Figure 1: Can you change color of Y010 and Y011 to green for consistent to Y001 and Y101?