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: INVESTIGATING THE RELATIONSHIP BETWEEN INTERGROUP PHYSICAL CONTACT AND ATTITUDES TOWARDS FOREIGNERS: THE MEDIATING ROLE OF QUALITY OF INTERGROUP CONTACT
Review round: 1
Reviewer: 1

Output:
Basic reporting: This paper examined with a single study whether the Experienced Intergroup Physical Contact (EIPC) increase positive attitudes towards an outgroup (i.e. foreigners) by mean of the quality of the intergroup physical contact.

The paper touches a topic highly relevant and timely: prejudice towards foreigners and ways to reduce it. It is well written and clear. The structure conforms to the standard sections in a scientific paper. It includes a table and a figure and the authors share raw data.
However one of the main weaknesses of it is that it did not review highly relevant prior research about the main topic of the manuscript, as for example the work done by Choma, Charlesford & Hodson (2014) or Hodson, Dube & Choma (2015). Furthermore, in the introduction nothing is said about the extensive literature on embodied cognition that is also relevant when analysing the relation between physical contact and prejudice. Therefore, it is not clear if the current study adds enough to the field. It is seems that the most important point that the paper adds to the prior research has to do with one of the mechanisms that could explain why physical contact can improve intergroup attitudes: the quality of this physical contact. However, the authors predicted upfront this mediation but there is hardly any justification of this prediction, therefore it is seemed more a postdoc one.

Another important pitfall of the paper has to do with the lack of specification about who were the participants thinking about when they were asked about foreigners. From my point of view it is not the same to think about immigrants who move to find better life conditions in a new country and are usually targets of prejudice than about high class tourists who travel for holidays but are usually by natives. From my point of view it would be much more interesting if the research would have focused just in negatively evaluated outgroups.

Minor point:
The format of the figure seems a bit odd. It is too big and uses colours to show the coefficients of each path, however usually figures for mediation analyses used black and white graphs.
Experimental design: The paper fits well within the aims and scope of the journal. The research question is properly defined, but as I said previously, although authors posited a knowledge gap that the paper tries to fill, this gap it is not clear to me if you take into account the previous work (including the one not reviewed by the authors).
The research fits with ethical standards in the field.
The method described is enough to allow replication, but the measures used have a limited scope as the scale used to measure experienced physical contact is built for the present research and not adequately validated.
Validity of the findings: The results seems to be statistically sound, however the manuscript presents just one main study and its hypotheses were not pre-registered and it did not show a neither a prior power analysis to determine the sample size nor a post-doc one in order to determine the power of the study given the sample size used.
It just presented a correlational study (plus a pilot one), and therefore the conclusions are very limited, although the author acknowledged it. The pilot study seems to have the goal of building and validating the EIPC, however the authors did not perform the standard process of scale building and validation.
Additional comments: In my opinion the paper would add significantly more to the field if it includes an experimental confirmatory study that replicates the results of the mediation showed in the main study of the paper.


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: INVESTIGATING THE RELATIONSHIP BETWEEN INTERGROUP PHYSICAL CONTACT AND ATTITUDES TOWARDS FOREIGNERS: THE MEDIATING ROLE OF QUALITY OF INTERGROUP CONTACT
Review round: 1
Reviewer: 2

Output:
Basic reporting: Reporting is ambiguous and its difficult to understand.
1.	The manuscript is replete with stylistic errors and it would benefit from some proofreading.
2.	Confusion of touch vs contact
3.	Race or ethnicity? “an African-American experimenter, reduced prejudice towards African-Americans, compared to (line 67) when participants did not receive any touch. In other words, this research demonstrated that 68 interethnic
Experimental design: The paper employs survey design but it does not discuss and convince the audience why is this the best method to investigate the topic. I was under the impression that this was manuscript based on experimental design  as they refer to “experimenter”. On a separate note I had a real struggle to understand the terminology the authors use to report their results. for instance (an in no particular order):
1.	What does it mean and what is “A causal mediation analysis using linear mixed effect (i.e., lme, fitted by minimizing the (line 200) restricted maximum likelihood criterion, Laird & Ware, 1982; see Rigutti, Fantoni, & Gerbino,201 2015, for a similar analysis) as mediator model types was performed to verify whether higher”
2.	Did the authors have an predictions regarding these? “used as two independent mediators, and outgroup attitudes as the (line 206) outcome variable, with participant gender and nationality treated as both fixed and random (line 207) effects in order to maximize the robustness of the mediation analysis over individual variability”
3.	Why 2000 resamples?
4.	What are the effect sizes for individual paths?
5.	What platform did the authors use to analyse their data?
6.	The model fit comparison appears to be a qualitative one as I don t see the results of a chi square comparison test?
Validity of the findings: The question itself is interesting but is there gap in the literature that the manuscript addresses?  How does the manuscript relate to the previous research and extend it? The introduction summarizes the literature on various themes of intergroup contact but I do not think it goes beyond replication of previous research, in fact only one paper, but it fails to identify the gap in this literature and to introduce the research question. What is it the authors want to show or claim? We should create conditions to facilitate people touching each other?
Why did the authors exclude the following participants?
Participants who did not answer to more than one item on the prejudice scale (n = 1) or who did (line 160) not report relevant information such as gender (n = 2) were excluded from the sample.
Additional comments: I read the manuscript titled “Investigating the relationship between intergroup physical contact and attitudes towards foreigners:the mediating role of quality of intergroup contact” ". The study investigates the impact of physical contact on outgroup attitudes via quality and quantity of contact. Given the popularity of intergroup contact theory this is an interesting area of research. As such, the manuscript has the potential to inform our understanding of the link between ideology and praxis with significant implications for education. Sadly, I do not think that this potential has been realized and I have certain concerns that prevent me from me from supporting the publication of the manuscript.  I outline these below.

Theoretical Novelty/Clarity: The question itself is interesting but is there gap in the literature that the manuscript addresses?  How does the manuscript relate to the previous research and extend it? The introduction summarizes the literature on various themes of intergroup contact but I do not think it goes beyond replication of previous research, in fact only one paper, but it fails to identify the gap in this literature and to introduce the research question. What is it the authors want to show or claim? We should create conditions to facilitate people touching each other?
Empirical Contributions & Methodology: The paper employs survey design but it does not discuss and convince the audience why is this the best method to investigate the topic. I was under the impression that this was manuscript based on experimental design  as they refer to “experimenter”. On a separate note I had a real struggle to understand the terminology the authors use to report their results. for instance (an in no particular order):
1.	What does it mean and what is “A causal mediation analysis using linear mixed effect (i.e., lme, fitted by minimizing the (line 200) restricted maximum likelihood criterion, Laird & Ware, 1982; see Rigutti, Fantoni, & Gerbino,201 2015, for a similar analysis) as mediator model types was performed to verify whether higher”
2.	Did the authors have an predictions regarding these? “used as two independent mediators, and outgroup attitudes as the (line 206) outcome variable, with participant gender and nationality treated as both fixed and random (line 207) effects in order to maximize the robustness of the mediation analysis over individual variability”
3.	Why 2000 resamples?
4.	What are the effect sizes for individual paths?
5.	What platform did the authors use to analyse their data?
6.	The model fit comparison appears to be a qualitative one as I don t see the results of a chi square comparison test?
Other Issues:
1.	The manuscript is replete with stylistic errors and it would benefit from some proofreading.
2.	Confusion of touch vs contact
3.	Race or ethnicity? “an African-American experimenter, reduced prejudice towards African-Americans, compared to (line 67) when participants did not receive any touch. In other words, this research demonstrated that 68 interethnic
4.	I am utterly confused by the claim that the “Quantity and quality of intergroup (line 99) contact have often been treated together, we reckon that dissociating these two aspects of” especially when this claim is followed by a review of research on the differential effects of quality vs quantity of contact

Why did the authors exclude the following participants?
Participants who did not answer to more than one item on the prejudice scale (n = 1) or who did (line 160) not report relevant information such as gender (n = 2) were excluded from the


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: INVESTIGATING THE RELATIONSHIP BETWEEN INTERGROUP PHYSICAL CONTACT AND ATTITUDES TOWARDS FOREIGNERS: THE MEDIATING ROLE OF QUALITY OF INTERGROUP CONTACT
Review round: 2
Reviewer: 1

Output:
Basic reporting: I appreciate the authors’ efforts to respond to each of our comments, most of which address the relevant concerns.

On the theoretical side, I think the manuscript in its current form does much better at discussing the literature that was not included in the first version of the manuscript and highlights the gap that the study intended to fill within it, specially regarding the contribution of intergroup physical contact in the field of intergroup attitudes and the mechanisms which can explain it. Furthermore, they now make much more explicit why they predict that quality, and not just quantity of intergroup contact, may mediate the relation between intergroup physical contact and intergroup attitudes.

Finally, still some typos and grammatical errors remain in some of the revised parts of the manuscript.
Experimental design: Methodologically, I am satisfied with the sensitivy analyses run in order to justify the sample size. However, from my point of view is not convincing the reasons why the authors decided to exclude some participants from the analyses (they said because they do not answer with “relevant information”). Therefore I strongly recommend to show the results without any exclusions. If the results remain the same, they would not have any problem, if this were not the case, they would have to try to explain the differences. In my view the authors solved the rest of the most important methodological issues I raised in my previous review.
Validity of the findings: That said, and although I am aware of the difficulty to gather more data from a confirmatory or experimental study, they should acknowledge this point in the limitations of the manuscript, specially the exploratory nature of their results.
Additional comments: Overall, I think this is an interesting set of findings indicating that physical intergroup contact could improve intergroup attitudes through the improvement of the quality of intergroup contact. However, in the manuscript it should be clear that this is just a first step and some more should be done in order to confirm this result and deep on causal relations between the relevant variables.


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: ANALYSIS OF RELATIVE ABUNDANCES WITH ZEROS ON ENVIRONMENTAL GRADIENTS: A MULTINOMIAL REGRESSION MODEL
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is well written and, in general, easy to read. However, there are some points that require a more clear explanation (see points below). Also references are adequate and relevant although they can be complemented for a more exhaustive bibliography (see points below). Figures are well presented and they are relevant. Raw data and R/Stan scripts are available.
Experimental design: The addressed research is essentially methodological and consists of introducing compositional data methods in the field of Ecology. In my opinion it is within the scope of the journal.

The main goal of the manuscript is to introduce the compositional (log-ratio) approach in environmental-ecological fields. Special mention deserves the introduction of compositional derivatives and their interpretation to extract conclusions form the model. Also the treatment of zero-counts through a regression model estimated in a Bayesian framework can be considered as a novelty in this context of modeling species composition.

The problem and data treated are of moderate interest but the methods applied to model the community evolution along the depth clearly justifies the publication of the manuscript.
Validity of the findings: Data provided by the authors allows replication of results. Their principal virtue is that they represent a quite frequent situation, a several species composition changing along a gradient in which abundant zero counts appear. The attained conclusions are sound apparently valid and well based on the fitted model.
Additional comments: First of all I liked the manuscript. The methodology is adequate to model the available data set in a successful way. However, I think that it can be improved in some directions described below. I consider that these possible improvements are not necessary for the publication but for gaining quality/clarity.

IMPROVEMENT LINES

Some concepts on the log-ratio approach to compositional data can be more carefully described and documented. Some points follow:

1. Page 6, lines 127-130.In environmental, health and ecological literature, there is a belief that the information contained in relative abundances and the so called absolute abundances is different. As samples are not exhaustive (in mass, in volume or size) the absolute abundances are also relative to that size or mass and they can be considered as proportional to the relative abundances. In compositional data analysis proportional sets of abundances are considered "compositionally" equivalent.

2. Equation of Aitchison distance (Section 2.4.3). The formula is wrong: a parenthesis with a square is lost. This equation can be extended to the expression in terms of the ilr-coordinates. This is, the square Aitchison distance is the ordinary Euclidean distance between the ilr coordinates. This expression is used afterwards but just commented (page 13, line 287; remember that the square norm is the square distance of a composition to the neutral element).

3. Page 10, lines 225-229. Here the authors present the clr-coefficients as a way of interpreting the model efficiently. Being this true, it seems that each clr-coefficient is related to a single component of the composition (taxon). The sentence "Thus a constant slope on the clr scale corresponds to constant proportional change in the relative abundance of a given taxon" contains this association taxon-clr coefficient, and attributes the detection of "proportional change" to clr scale. Any log-ratio coordinate has this property, particularly the ilr coordinates used to fit the model. The problem with the slope in the clr scale is that this slope changes with the subcomposition (set of taxa) analysed.

4. Page 10, line 209. In order to fit the model, abundances are blindly ilr transformed. Although this is acceptable, the opportunity of interpreting the ilr-coordinates is lost. The design of a sequential binary partition (SBP) (Egozcue & Pawlowsky-Glahn 2005, Pawlowsky-Glahn et al. 2015) produces a set of balances as ilr coordinates. These balances can be easily interpretable in terms of equilibria between groups of taxa. This can be more efficient than the interpretation in terms of clr coefficients commented in point 3. On the other hand, linear change on compositions straight lines in the ilr-coordinate space (the clr-space is identical to that of ilr-coordinates).

5. Definition of compositional data (Abstract line 7; page 2,line 19). The authors use the early definition based on the constant sum of a vector of positive components. Nowadays, compositional data are better described as equivalent classes of proportional vectors with positive components. This leads to the conclusion that any composition can be represented as a constant sum vector but this representation is neither necessary nor sufficient condition for using the log-ratio approach for compositional data (e.g. Pawlowsky-Glahn et al. 2015, Barceló-Vidal and Martín-Fernández 2016.)

6. Although references are adequate they can be completed in some aspects. Some suggestions for additional references, most of them authored by me (J.J.Egozcue):

The name "Aitchison Geometry" and also "metric variance" and "metric centre" were firstly introduced in

Pawlowsky-Glahn, V. and J. J. Egozcue: Geometric Approach to Statistical
Analysis on the Simplex, Stochastic Environmental Research and Risk Assessment,
15, 5, 384-398, 2001.

Agreeing that compositional methods have low impact within the ecological literature, consider this reference where compositional methods are used:

R. López-Flores, X. D. Quintana, A. M. Romaní, Ll. Bañeras, O. Ruiz-
Rueda, J. Compte, A. J. Green, J. J. Egozcue: A compositional analysis
approach to phytoplankton composition in coastal Mediterranean wetlands:
Influence of salinity and nutrient availability. Estuarine, Coastal and Shelf
Science, 136, 72-81, 2014.

Fitting compositional differential models (not Bayesian) have been studied in

Egozcue, J. J. and Jarauta-Bragulat, E.: Differential Models for Evolutionary
Compositions, Mathematical Geosciences, 46, 4, 381-410, 2014.

An updated summary of compositional methods (including differential equations) can be found in

V. Pawlowsky-Glahn, J. J. Egozcue and R. Tolosana-Delgado: Modeling
and Analysis of Compositional Data, John Wiley & Sons, Chichester, UK, 2015

7. The description of the Bayesian model used is passed to supplementary materials. In my opinion a brief reference on the observational model and its main assumptions (residuals in ilr-coordinates are normal) can be presented in the body of the paper.


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: ANALYSIS OF RELATIVE ABUNDANCES WITH ZEROS ON ENVIRONMENTAL GRADIENTS: A MULTINOMIAL REGRESSION MODEL
Review round: 1
Reviewer: 2

Output:
Basic reporting: In this manuscript, Fiona Chong and Matthew Spencer present a dataset that utilizes video imagery to survey taxonomic variation as a function of depth and demonstrate that a compositional data analysis (CoDA) that is based on the “algebra of compositions” can successfully be applied to this dataset.  This manuscript is timely as there has been a good deal of recent interest in how compositional artifacts can distort analyses of ecological datasets.  The algebraic notation in the manuscript is dense and while this is perhaps unavoidable in may make the paper somewhat inaccessible to the target audience of experimental ecologists.

1. Basic Reporting. The authors sufficiently motivate the importance of compositional considerations when working with ecological data. The discussion of the compositional data analysis aspects was generally well executed.

-	It may be of benefit to ecologists reading this article to be clear about the limitations of compositional data. This primarily comes about by the fact that with such relative data one is unable to know if an increase in relative abundance is due to an increase in the population of that taxon, all other taxa held constant, the maintenance of that taxon’s population given a decrease in other taxa, or a decrease in the population of that taxon with other taxa decreasing to a greater extent than the apparently “growing” taxon. This discussion may be helpful near lines 287-289.

-	The addition of discussion regarding the interpretability problems surrounding the ILR and the potential mathematical limitations of the CLR is warranted.

-	More detail about the Monte Carlo Markov chain resampling scheme should be put in the main paper.

-	Figure 2: The caption is currently lacking information on the pseudo-count used in the CLR transformation. The changes in the y-axis scales of the inset images can potentially be misleading. It is suggested that the authors either set the scales to be uniform across all panels or add a supplemental figure with such a view of the data.

-	Figure 6: A zoomed inset image within this figure or a supplemental figure showing the mean relative abundance of rare taxa would be helpful in providing a visual component to the discussion of the 95% HPD intervals for these taxa. This is currently difficult to decipher because of the fixed scaling with the more abundant taxa.

-	Figure 1: Which imaging system (the ROV’s camera or the GoPro) was used to capture these images? The figure also appears to blur to various extents across the different depths.

-	Figure 3: If (a) and (b) are symmetric along the diagonal, then compositing the 2 figures into one along the diagonal may enable readers to better discriminate similar coordinates between the fine gradations in the two figures which is difficult to do currently. Figure 3 as currently presented is quite difficult to interpret.

-	Figure 4: The caption may be missing information on the numerical bounds of each variable which may aid in its interpretation by readers less familiar with CoDA methods. The additional of tick marks along the axes may offer similar help.

-	Supplemental Figures and Tables: In order to avoid potential confusion, it may be necessary to reiterate that the p - 1 (8) ILR coordinates have no simple interpretation in terms of the (8 taxa + 1 wall = 9) initial p coordinates.
Experimental design: 2. Experimental Design.
	The main thesis of the manuscript is that analyses based on “compositional algebra” can give important insights into ecological data.  This thesis would be considerably strengthened if the authors could contrast their analysis with the kind of standard analyses used in the ecological literature.  How does their analysis compare to a simple linear model fit directly comparing a polynomial based on depth to the number of counts? Does a PCA or MDS ordination yield imperfect separation between depths that the authors’ pipeline is better able to discern?  Some direct comparison of the newly developed pipeline to standard techniques (which the authors claim are misapplied in the literature) would increase the potential impact of the manuscript. The authors assert that “Most of the popular measures of community dissimilarity are not perturbation invariant, and are therefore misleading.” While this detail is technically correct, their paper would be strengthened by a demonstration of an incorrect biological conclusion that was drawn from such a “misleading” procedure and that their method produces a correct interpretation.
1.	Can the authors be more explicit about whether they used a pseudo-count?  The discussion of pseudo-count information for the CLR transformation is currently missing (lines 225-229). This is especially important information as the CLR transformation is used on rare taxa that likely have 0 values, which would lead to a geometric mean denominator to be 0. Given the small number of different taxa, it may be also be worthwhile to assess the behavior of the models given different pseudo-count values. Having this information would be especially helpful in the interpretation of Figure 2. The authors also do not discuss pseudo-count for the Aitchison norm which is warranted given its reliance on the geometric mean like the CLR transformation.

2.	The description of the data collection process was difficult to follow and may be much improved by the addition of a simple diagram visualizing the sample collection and image analysis steps taken. It is also not clear what steps in the identification of organisms from the video and images captured were through automated image analysis or human visual curation (lines 171-176).

3.	The authors mention the constraint on the number of points sampled always being 100 per still image (lines 195-198), but they also state earlier that they have removed two rare taxa from the analysis (lines 186-187). Were these points resampled as was the case for points that could not yield positive identification or were there, in fact, a few samples that had less than 100 points?
Validity of the findings: Validity of the Findings

The authors investigated the depth-dependent changes in community structure using perturbation-invariant techniques from the treatment of the relative abundance as compositional data. They reiterate the suitability of CoDA techniques for ecological data and encourage its increased usage by ecologists in arguments that attempt to tie together mathematics and biology. They also offer several ecological hypotheses explaining the dependence of community structure with depth.

1.The difficulties encountered during the data collection process regarding the failure of the ROV’s distance finding capabilities (lines 157-160) bring up questions regarding the robustness of the data. The authors assert that problems involved in their data set are unlikely to introduced errors in the analysis (lines 160-161), but they need to provide evidence supporting this claim.  In particular, the claim that “the field of view was always large enough to contain many organisms, so the relative abundances are unlikely to depend on the exact area sampled” seems poorly justified.
2.It may best serve the ecologists who can potentially benefit from using the methods outlined in this article if the authors also include a secondary “classic” dataset from a source such as Legendre and Legendre. Such a replication dataset would enable their audience to be able to readily compare and contrast this method of analysis to traditional ones.

3.The statement calling into question the “classical picture of intense competition for space determining the structure of subtidal marine communities” is speculative. There are numerous microbial biofilms that may render such sections of habitat (“blank wall”) unsuitable for the growth of organisms documented in this study. Furthermore, there is the classic example of the “no man’s land” that forms between two competing colonies of sea anemones which is apparent barrenness that is the result of an intense competition for space.

4.	Per PeerJ’s policies, all scripts and raw data should be made publicly available, and the video recordings were not among the material provided.  This seems particularly important in a paper such as this one which seeks to introduce a new method.
Additional comments: Optional:  The impact of the paper might also be substantially improved if the authors could demonstrate that their techniques worked on sequence/count datasets since many ecologists use these kinds of sequencing experiments to survey microbial diversity.  There is for example a 16S sequence dataset that has been published  ( https://www.nature.com/articles/ismej200986 ) that surveys microbial diversity as a function of depth.  Applying the proposed analytical framework to such a dataset would potentially be of interest to ecologist, but may be outside the scope of the paper so is here included as an optional note to the authors.


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

Input:
Title: ANALYSIS OF RELATIVE ABUNDANCES WITH ZEROS ON ENVIRONMENTAL GRADIENTS: A MULTINOMIAL REGRESSION MODEL
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: In page 17, line 283, Equation of Aitchison distance, last right-hand-member: there is a typo. The last x should be subscripted as  x_{2,j}    .

I feel that your paper is an excelent contribution to the compositional data analysis.


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: ANALYSIS OF RELATIVE ABUNDANCES WITH ZEROS ON ENVIRONMENTAL GRADIENTS: A MULTINOMIAL REGRESSION MODEL
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The manuscript is much improved in clarity over the previous version and I have no further requirements for revision.

The below notes are minor and should be considered as optional suggestions:

Bray-Curtis is a dissimilarity and not a true distance as it does not preserve the triangle inequality.

The authors may find the following reference helpful in regards to the discussion of the using the Aitchison distance in dissimilarity analyses on lines 82-85: Microbiome Datasets Are Compositional: And This Is Not Optional (Gloor et al., https://www.frontiersin.org/articles/10.3389/fmicb.2017.02224/full), as the authors of that work similarly emphasize said point.

While not necessary suggested references for this manuscript, the authors may find the following R/python packages insightful for future work in aiding the biological interpretation of ILR balances: A phylogenetic transform enhances analysis of compositional microbiota data by Silverman et al. (https://elifesciences.org/articles/21887) and Balance Trees Reveal Microbial Niche Differentiation by Morton et al. (https://msystems.asm.org/content/2/1/e00162-16)

The authors may also find this methodology regarding Bayesian methods in analyzing compositional microbiome data helpful in future work: Unifying the analysis of high-throughput sequencing datasets: characterizing RNA-seq, 16S rRNA gene sequencing and selective growth experiments by compositional data analysis by Fernandes et al. (https://microbiomejournal.biomedcentral.com/articles/10.1186/2049-2618-2-15)


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: GEOPOLITICAL SPECIES REVISITED: GENOMIC AND MORPHOLOGICAL DATA INDICATE THAT THE ROUNDTAIL CHUB GILA ROBUSTA SPECIES COMPLEX (TELEOSTEI, CYPRINIDAE) IS A SINGLE SPECIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is written in clear, unambiguous, professional English throughout.

The introduction & background show context. The context is the extraordinary confusion created by previous inexpert and inadequate species descriptions and taxonomic revisions. The authors are admirably restrained in their criticism of this taxonomic confusion.

I’m not an expert on these fishes, so I wouldn’t be able to tell if the referencing was inadequate or missing key citations to important previous work. The referencing throughout (especially in the taxonomic summary) seems to be comprehensive.

The taxonomic revisions by Rinne seem to be a really important source of the extensive taxonomic confusion surrounding species of Gila. So I was a little distressed to find that none of those papers (Rinne 1969; Rinne 1976; Rinne & Minckley 1970) is in the References list. From mousing around I think Rinne 1969 is his Masters thesis at ASU; and Rinne 1976 is his article in the Wasmann Journal of Biology? Also there is a typo on line 825: “Tosada” should be “Posada”.

The structure conforms to PeerJ standards and norms for this type of phylogenetic taxonomic study.

The figures are relevant, clear, and informative. There are some errors in the figures. The legend for Fig. 1 says “stars represent locality of type series for G. robusta (red) G. intermedia (black) and G. nigra (blue)” but there are no stars; I think the authors mean the squares? The type locality for G. robusta is outside of the map area and is not shown on a specific drainage, which seemed confusing. Also the site number 122 (the collection location for the individual called “122 O’Donnell Canyon” in Fig. 2) is not shown in Fig. 1. Similarly, the collection locations for the G. cypha and G. elegans individuals is not shown in Fig. 1 or described in the text.

Raw data were supplied.
Experimental design: The paper is based on original primary research that falls within the scope of the journal.

The research question is well defined, relevant & meaningful. It includes a clear statement on how the research fills an identified knowledge gap.

The study is based on rigorous investigation performed to a high technical & ethical standard. This type of study is exactly what RADseq methods were developed for: the volume and quality of data generated by this method for this study gives the authors a lot of power to test the three-species hypothesis as well as to explore patterns within those data that might be more consistent with other hypotheses. The data in this study are state-of-the-art.

The methods are described with sufficient detail & information to replicate. However, I did not understand how the authors gave provisional species names to the newly collected individuals that were the material for the morphological and genetic data collection. The text (lines 224-227) says that “Due to the problems associated with the taxonomic key (Moran et al. 2017) the current practice of species identification for managers and researchers working with the G. robusta complex within the Lower Colorado River Basin is based on drainage location. We follow this convention because no alternative method of assignment is currently available.” It makes sense that this is the current practice. But it was hard to understand from the map in Fig. 1 how this worked for the authors in this study. For example, some of the red locations for G. robusta (labelled 141 and 145 in Fig. 1) come from the southern drainage that includes the G. nigra type locality (the blue square) as well as one of the G. intermedia locations (125). Also the type locality for G. robusta (the red square in Fig. 1) is off the map and not shown on a specific drainage. Maybe this means I just don’t understand what ‘drainage’ refers to: is each of the light blue lines in Fig. 1 a single drainage? Or do collections of light blue lines leading to one of the dark blue lines form a single drainage? I needed a more complete and clear explanation of this working definition of how to apply the three provisional species names to individual fish. I realize that this is in essence the problem the authors are trying to sort out, but the starting point for the reader’s understanding of the study is an understanding of how one of the three provisional species names was applied to each individual fish that was collected for the genetics and morphological parts of the study. I didn’t understand how that was done. Possibly what I needed was an additional figure that shows the geographic ranges of the three nominal species mapped onto that same illustration of river drainages in Fig. 1, maybe with the individual creeks and larger tributaries colored red, black, or blue to show which ones harbor G. robusta, G. intermedia, or G. nigra.
Validity of the findings: The data are robust, statistically sound, & well-controlled. I had two questions about the data analysis. These are also my only substantive criticisms of the study and interpretation.

First, if the individual fish sampled for this study all come from a single biological species (as the authors propose), then recombination among many of the contigs from the ezRAD data should have scrambled their genealogical history. The authors argue (lines 552-553) that they have found “evidence for five distinct clades that may correspond to geography more than currently accepted taxonomy.” The authors claim in the Discussion (lines 596-599) that “Our data do not indicate a single well-mixed population across the Lower Colorado River Basin. In fact, clear genetic structure exists among many of the populations analyzed (especially between the five well-resolved clades), but this population structure is not aligned with the three currently recognized taxonomic units.” Because recombination obscures genealogical relationships, I think these statements are far too strong and are not supported by the data.

For samples of many unlinked loci from across the genome (such as ezRAD contigs), analyzing all those unlinked loci by concatenating the sequences together (as if they all came from the same single sex chromosome or some other single nonrecombining unit or haplotype) within each individual does not give a very meaningful illustration of the history of those individuals or their genealogical relationships to each other. Instead, each of the ezRAD contigs has its own genealogical history that is independent of the other contigs because of recombination and independent assortment. This is the problem with phylogenetic thinking in a population context for sexual organisms. For example, imagine that individuals 100 and 150 swam downstream, met, and mated in the main tributary that they share (the dark blue line to the lower left of those two labeled black points in Fig. 1). Their offspring would have half of the contigs from 100 and half from 150, and it seems unlikely that a phylogenetic analysis of those two sets of mixed ezRAD contigs (like the analysis presented in the manuscript) from those offspring would correctly assign those offspring to either clade 1 or clade 2, because recombination within the two parents would scramble the apparent signal of phylogenetic relationships among those offspring relative to the parents and relative to the other 15 sampled individuals.

So I don’t agree with the authors that these five clades are real entities, that they are possibly about to evolve into new species, or that they represent promising targets for conservation efforts. The five clades seem likely to be artifacts of concatenating together the phylogenetic signal from hundreds of ezRAD contigs that in nature are unlinked due to recombination and independent assortment (and have no real phylogenetic signal when concatenated together as if they were linked). Unless I have badly misinterpreted the methods, this seems like a really surprising error for the authors to have made (especially the senior authors who are experienced and skilled population geneticists). So I apologize if my criticism is based on a misunderstanding.

I think a coalescent analysis (instead of a phylogenetic analysis) that uses each of the gene trees from all of the (presumably unlinked) contigs seems like a better analysis. Could the authors consider doing that population genetic (rather than phylogenetic) analysis? It would be a nice complement to the clustering analysis proposed in my next comment below. Or, again, possibly this is an analysis for a different paper. Either way, I think at the very least the authors need to address the problem of recombination among unlinked ezRAD contigs and explain or account for how such recombination might influence their interpretation of a phylogeny of individuals in which unlinked parts of the genome are treated as if they were all linked in one long haplotype. I think that phylogenetic analysis is wrong (based on concatenated haplotypes of unlinked loci), so again at the very least the authors need to convince me (and other readers) that this phylogenetic analysis is relevant and informative.

One possible approach would be to treat the three sets of samples of the nominal species as possibly interbreeding populations, and fit isolation-with-migration models to the multilocus ezRAD contig alignments (using each contig as a locus). The authors could use those models to ask whether the population divergence times among robusta, intermedia, and nigra are detectably different from zero (that is, whether there really are three distinct populations or species that have been evolving independently); they could include the mtDNA haplotypes as an additional locus, one with a reasonably well-known mutation rate, and use that mutation rate calibration to convert the model parameters to population units (especially to convert the divergence time estimates to years). That kind of analysis could be done using IMa2, or (maybe even better) using one of the ABC methods.

The authors argue (lines 599-600) that “Our study was designed to examine a phylogenetic question and sampling was not sufficient for addressing population level questions”, but intensive sampling of individuals is not required for IMa model-fitting. Those models depend mainly on deep sampling of genomes (loci), which ezRAD does very well. I think the authors’ data are well suited to an isolation-with-migration analysis.

Second, the analysis of the genetic data seems to show that no clades consisted solely of individuals from one of the three ‘species’. On that basis the authors conclude that all of those individuals should be assigned to one species name. That may be an appropriate conclusion, but that analysis only shows that none of the three ‘species’ forms a monophyletic group; the analysis doesn’t consider whether there are multiple genetically distinctive clusters of genotypes within those data. Asking whether there are distinctive multilocus genotype clusters is not the same as asking whether there are long branches in the concatenated gene tree (Fig. 2). The authors argue that these five distinctive clades in Fig. 2 might be important evolutionarily distinct units, but I argued above that this phylogenetic analysis seems flawed.

As I read the description of the data collection I was sure the authors would eventually describe how they carried out a STRUCTURE analysis or some other multilocus clustering analysis that would help them decide whether the fish they sampled cluster into one or more than one distinctive group of multilocus genotypes. But that analysis isn’t in this manuscript. If that’s an analysis for another paper, then that would be ok. But it would be great if the editor wants to encourage the authors to add that population genetic analysis to the phylogenetic analysis presented in the submitted manuscript. That clustering analysis would be a nice complement to the isolation-with-migration model fitting that I suggested above. Those analyses together would go a long way toward testing the authors’ assertions that (1) the three named species taxa are not monophyletic clades AND (2) all individuals belong to one cluster of genotypes that represents a single biological species.

At this point in writing the review, I wanted to look at some of the recent molecular studies that have previously tried to sort out this problem, including Schonhuth et al. 2012, 2013; Dowling et al. 2015; and Marsh et al. 2017. But again none of those four articles is in the References list. It seems important, especially in an article like this where the goal is to sort out problems in the previously published literature, for the authors to carefully check all of the literature citations in the text and match them to all of the items in the References list.

The conclusions are well stated, linked to the original research question, and limited to supporting results. I thought there might be one feature of both the review (of the taxonomic history) and the interpretation of the phylogenomic patterns that could be expanded on. The authors note in several parts of the text that the genetic data are not consistent with phylogenetic patterns expected to be produced by processes acting on several reproductively isolated species. And in several places in the text the authors note the possible contribution of hybridization to account for some of the observed genetic and morphological variation. But the authors don’t say anything specific about knowledge of actual reproductive isolation (or reproductive compatibility) among individual fish from different populations for any of the three named species taxa (robusta, intermedia, nigra). Maybe the reference to heritability of phenotypic differences (lines 544-545) is a reference to reproductive isolation and hybridization? Is nothing known about whether males and females from these different locations or ‘taxa’ can mate with each other? If (like some other fishes) gametes can be artificially stripped from adults, can ‘hybrid’ offspring be produced by artificial insemination? Are fertilization rates or other measures of gametic compatibility lower for ‘hybrid’ crosses than for ‘conspecific’ crosses? What do those ‘hybrids’ look like?  Are they viable? This seemed like an obvious important gap in knowledge: if the gap is real, the authors should be encouraged to highlight it prominently. If the gap is only apparent, the authors should be encouraged to fill it in by reviewing previous studies of gamete compatibility, mating behavior, viability and morphology of hybrids, or other direct evidence for reproductive isolation.
Additional comments: The lengthy quotation from the note appended to USNM 246 (lines 98-101) is remarkable. If it’s possible, could the authors consider adding to the manuscript a figure that shows a photograph of that note? Maybe that’s not very valuable as data, but as an interested reader I would have loved to see the actual 1945 note itself in R. R. Miller’s handwriting as a sort of historical artefact. The subsequent paragraph (lines 103-119) is again remarkable: taxonomy is hard enough, but the extent of taxonomic confusion about these fish that was created by the biologists (rather than by the biology) seems extraordinary.

As an aside, I’ve worked with some museum collections but never with an accession number so low. These are old, important, original fish collections!

Lines 58-62: The paragraph seems out of place: it refers to hypotheses used to account for patterns, but the patterns haven’t been described yet. The reader doesn’t know what ‘patterns’ are until after reading the section ‘Systematic and taxonomic review’ (which is excellent). Maybe instead of “invoked to explain the observed patterns” it might help to say specifically “invoked to account for geographic variation in morphological and ecological traits within and among species of Gila.”

Lines 79-80: “in part due to the reliance of population means as diagnostic characters and variance among individuals within and among locations.” I think the authors mean “in part due to the reliance on populations means as diagnostic characters, and in part due to confusion arising from variation [not variance] among individuals within and among locations.”

Lines 401-403: “For example… only 28% of the 32 morphological characters examined (Table 1,2) aligned with the types of G. robusta, but instead 63% aligned to G. nigra and 51% to G. intermedia (Table 3).” That seems to add up to 142%, so I think the sentence needs to be rewritten or maybe broken up into two sentences that correspond to two different variables or quantities (I think that’s the source of the confusion but I can’t tell from the context of the sentence).

Part of the text (lines 396-408) seems to be in gray rather than black font?

Line 433: Spell out Gila to avoid starting the sentence with an abbr.

Line 451: “name-bearing”, not “name bearing”.

Line 475: “let alone” is too colloquial here.

Lines 501-516: “current taxa” is potentially confusing because the previous paragraph discussed topics related to the speed or velocity of water flow (i.e., water currents); maybe use “present-day taxa” instead? Similarly, “drift” has a hydrological as well as a genetic meaning; maybe use “genetic drift”?

Line 543: Indent for a new paragraph here?

Line 582: In this sentence “codified” and “Code” are redundant: the C in ICZN stands for Code. Instead how about “as applied through the rules prescribed by the ICZN.”

Lines 573-588: This discussion of the idea of geopolitical species was interesting and useful. It seemed to me while reading this paragraph that part of the problem is specific to the US Endangered Species Act and its emphasis on conservation at the level of taxonomic species. Is this a universal problem, or is it more relevant to conservation problems and priorities in the USA (I don’t know because I’m not a conservation biologist and not an American)? Maybe the authors could highlight this problem as part of the explanation for motivated reasoning on the part of taxonomic splitters?

Lines 589-590: “To be perfectly clear” is too colloquial.


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: GEOPOLITICAL SPECIES REVISITED: GENOMIC AND MORPHOLOGICAL DATA INDICATE THAT THE ROUNDTAIL CHUB GILA ROBUSTA SPECIES COMPLEX (TELEOSTEI, CYPRINIDAE) IS A SINGLE SPECIES
Review round: 1
Reviewer: 2

Output:
Basic reporting: Nicely written, bogs down in the details of the taxonomy, some of which might be better served in references to other treatments of similar scope.

I pointed out a couple of issues with citations.

Rather than colors, could you include the 'putative' species designation on the phylogeny to show polyphyly more readily?
Experimental design: see comments below
Validity of the findings: Im not so sure that these data add much to what has already been done, but it is nonetheless a cohesive body of work that includes a variety of molecular and morphological approaches.  To that end, the authors are quite convincing that robusta should be recognized but other species subsumed.
Additional comments: Copus et al.

Geopolitical species revisited: Genomic and morphological data indicate that the Roundtail Chub Gila robusta species complex (Teleostei, Cyprinidae) is a single species

Minor edits and Queries:

L27:  		(~ 90% complete) - not sure if this is useful here

L48:		citation or description (assume both?)

L58-62:	This is an awkward paragraph, that contains too little information to stand as on its own.  Suggest appending to following paragraph.

L101:	Not getting how this relates to taxonomic confusion unless youre implying that J&E thought these were cods.  Appear to be more clerical errors.

L109:	from the Zuni River

L122:	G. intermedia has a complex taxonomic history (this isn’t necessary here)

L151:	gets a little confusing, maybe add a reference for ‘original description’

L154:	Why not sufficient?

L224:	This should be somewhere in the introduction with an explanation of why individual characters are not useful

L248:	might indicate in parentheses which were standardized by what (since the table is supplemental)

	Do any of these morphological measurements bear on the aforementioned “the inferior fins especially are quite small”

L255:	greater than 10Kb?

L265:	manufacturers’

L267:	to 1μg of template DNA (something seems missing here)

L284:	curious, are there any potential issues with orthology/paralogy?

L286:	paired

L306:	done by position or just wholescale by locus?  Why not retain the mixed model of mtDNA and nDNA in the phylogenetic analyses?

L378:	Rather than looking for individual characters, could you represent this in space via a PCA, or is the number of specimens versus the number of characters an issue?

L427:	I am confused by what is meant here, what exactly are you comparing?  I think, by the table, you are calculating means or comparing ranges by molecular clade, correct?

L442:	first mention of reproductive isolation, how measured?  I’m guessing this was simply inferred?

L443:	this is interesting, is the inability to discriminate limited to fresh materials (with wider geographical distribution), or does this extend to both data sets.  Any evidence that this issue is more applicable to the fresh versus the archival specimens?

L447:	Answers comment above, but note that this should be reinforced in the results where there is little attention to the fact that such differences in fact might exist in the types (unless you are arguing the converse, but I didn’t get that impression)

L454:	see comment L378 above, I believe this would be a more robust analysis than unitary characters, at least as a means to visualize ‘morphospace’

L475:	see L443 comment above.  Some of this discussion is a bit disjunct, and might be placed together for a better reading mss

L460:	Is there any chance that more recent hybridization might have obscured whatever might be seen in the types?  That is, are the types just as confusing as the fresh material?

L495:	Important to detail which concepts you’re talking about, unless of course, you’re implying that the current data wouldn’t support any commonly held concepts

L497:	Kind of a strawman without presenting the basis for how cryptic speciation was actually diagnosed by Marsh

L526:	Marsh et al. is not in citations

L527:	with all of the available information, would coalescent type approaches be useful?

L599:	This is a salient point, suggesting how this manuscript is predominately molecular in scope, exhaustive and important, but most of the manuscript focuses on the morphology.

L605:	Would be best to include this in the introduction somewhere.

L610: 	Do other of the more recent treatments (Marsh in particular) bear on this as well – is that manuscript perhaps better with more comprehensive morphological sampling?  I think a lot of this belongs in the introduction, no matter how awkward that might be to write

L768:	citation repeated (should be Marsh 2017?)

Overall:  My impression of this manuscript are favorable to a large extent, but there exists some confusion over what has been done already (new morphological analyses by March, all of the pre-existing molecular data) and what exactly this manuscript adds to the question of species validity.  I think the manuscript could do with a tightening of the Introduction, touching on what has been done historically (and especially more recently, e.g., Marsh and Page), and what value the huge amount of molecular data adds to the discussion.  The authors are quite convincing that fresh materials do not support any species boundaries as previously defined, at least morphologically (although sample sizes are very small), but it seems from reading the discussion that this is a foregone conclusion from what has been done recently.  What is new here, and I believe might be the better focus, is the large amount of concordant nuclear and mitochondrial DNA data and the phylogenetic analysis that it affords.


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: GEOPOLITICAL SPECIES REVISITED: GENOMIC AND MORPHOLOGICAL DATA INDICATE THAT THE ROUNDTAIL CHUB GILA ROBUSTA SPECIES COMPLEX (TELEOSTEI, CYPRINIDAE) IS A SINGLE SPECIES
Review round: 2
Reviewer: 1

Output:
Basic reporting: I'm satisfied with the authors' thorough and positive response to my previous review and comments.
Experimental design: I'm satisfied with the authors' thorough and positive response to my previous review and comments.
Validity of the findings: I'm satisfied with the authors' thorough and positive response to my previous review and comments.
Additional comments: Thanks for a very thorough revision. This is the kind of interaction with authors that makes peer review worthwhile for me.

I had just one additional comment (not a criticism). The authors included an example of their STRUCTURE results in the cover letter, and argued (convincingly) that their sample of individual fish is too small to justify publishing this analysis. I agree. But I wanted to comment on the quality of that result. Although I'm not an expert on this type of clustering analysis, I think these STRUCTURE results are actually consistent with all of the authors' other phylogenetic and population genetic results. If I understand the two data graphics, *all* of the individual fish had intermediate probability of assignment to one or the other of the k=2 groups (in each of the data graphics, every fish has a large blue region and a large orange region), and none of the fish was assigned with a high probability to either group (which would be shown in the graphic by a bar with mostly blue or mostly orange). This is a common result for STRUCTURE analyses where the model is overspecified and the number of groups in the analysis (k=2) is larger than the actual number of biological groups (k=1 in the case of Gila robusta).

I don't think that's necessarily a reason for the authors to add the STRUCTURE analysis and result to a second revised manuscript, but it seemed worthwhile to add that comment (and encourage the authors to follow up with more data if they are not going to publish these population genetic analyses now).


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: GEOPOLITICAL SPECIES REVISITED: GENOMIC AND MORPHOLOGICAL DATA INDICATE THAT THE ROUNDTAIL CHUB GILA ROBUSTA SPECIES COMPLEX (TELEOSTEI, CYPRINIDAE) IS A SINGLE SPECIES
Review round: 2
Reviewer: 2

Output:
Basic reporting: A very nicely written manuscript that I believe has improved from the original submission.  That taxonomic confusion with little basis for differentiation among taxa reigns historically is clearly presented and that presentation is without bias, making the manuscript rather neutral - this is a strong point of the submission.  The presentation is eminently fair and thorough.  The authors' contention that they sacrificed the data in lieu management (e.g., offered the data in a symposium) is well taken and satisfies the criticism that nothing new is presented here.
Experimental design: Design is solid, no issues have arisen since the first submission.  The inclusion of the coalescence analyses is a strength.
Validity of the findings: Strong and obviously supported by the morphological and molecular data presented.
Additional comments: Nice job dealing with a politically charged issue.  The fairness by which the data and conclusions are presented make the manuscript rather neutral, and that is a strength.


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: PRE-IMAGINAL CONDITIONING ALTERS ADULT SEX PHEROMONE RESPONSE IN DROSOPHILA
Review round: 1
Reviewer: 1

Output:
Basic reporting: Overall, the ms is very well written and easy to follow. The METHODS, however, do not contain sufficient details that would allow one to replicate the study. Examples include the food recipe (line 87) “yeast / cornmeal / agar medium” includes no amounts and very likely omits ingredients. Further details about the fly lines would be helpful, e.g., what is the “Di2/w1118 line” and why was it used? I understood it, but many readers may not.
Experimental design: I appreciate the large number of highly informative experiments. Two items that I would like to see more information about are the temporal structuring of treatments. That is, what treatments were tested simultaneously? This is crucial given the large temporal variation in such studies. Similarly, it would be helpful to know whether the courtship trials were conducted by observers blind to treatment.
Validity of the findings: Overall, I think that the ms reports a very intriguing phenomenon. There are two aspects of the experiments that the ms should elaborate on, justify and discuss. First, the use of decapitated females is very unnatural. Second, while recently mated females have some cVA on them, the ms describes a setting where cVA came from another source. Both these aspects make it very difficult to relate the results to ecologically and evolutionary relevant behavior.
Additional comments: The ms is written as if cVA on the eggs is the independent factor (e.g., Line 30: “We found that male courtship inhibition is strongest when male flies are derived from eggs covered with high levels of cVA.” Line 109: “to remove cVA from the egg…”. And the Fig. legends and captions) even though the ms acknowledges based on the results that an unknown substance must be the independent factor. I suggest the ms will focus on that substance throughout.

I don’t think that the definition of pheromones should include “innate stereotypical responses” (line 26). In fact, the start of the discussion contradicts this statement while citing Siegel & Hall (1979), who showed learning in the context of female chemical cues (as later documented by other studies). In general, courtship conditioning has been known to be a conditional phenotype affected by male age, mating experience and female availability.

Finally, the use of the term imprinting should be very well justified based on the critical discussions of this term and its appropriate use in the 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: PRE-IMAGINAL CONDITIONING ALTERS ADULT SEX PHEROMONE RESPONSE IN DROSOPHILA
Review round: 1
Reviewer: 2

Output:
Basic reporting: In the manuscript entitled "Larval imprinting alters adult sex pheromone response in Drosophila", Everaerts et al. reported that elimination of egg-coating-substances diminished courtship suppression effect of cVA at adult stage. Reintroduction of the substances rescued the cVA response, indicating that the presence of these substances at larval stage was required for pheromone response at adult. This is an intriguing finding and would provide an important addition to understanding how pheromone sensitivity is controlled. I have two main concerns that should be easily addressed by revision of the manuscript.
1. The authors' conclusion "male courtship inhibition is strongest when male flies are derived from eggs covered with high levels of cVA (Abstract, line 30~)" "adult male courtship suppression by cVA is a consequence of exposure to cVA (Conclusion, line 300~)" is overstatement and must be revised. Addition of cVA didn't change cVA sensitivity while introduction of the donor eggs recovered (Fig 1ef), suggesting the contribution of the unidentified egg-coating-substance(s) but not cVA. Though there is a possibility that a combination of several substances contributes to the effect and cVA is one of them, as the authors stated (line 75~), it should be described more carefully to avoid misleading. And with same reason, the term "imprinting" is not appropriate to describe the phenotype.
The cVA amount on the eggs and cVA sensitivity at adult (Fig 2) is a correlation, not a direct evidence showing a causal connection. There are many other components that are gradually lost in a mated female after mating, e.g. sex-peptide and other accessary gland proteins. Indeed, sex-peptide is known to be deposited on eggs.
2. Previous studies should be properly cited. The plastic control of cVA response have been reported in Liu et al. 2011 (aggression) and Tachibana et al. 2015 (courtship suppression), then this is not the first report and the introduction part should be revised accordingly (line 73~). A sentence from line 69 should be more accurate.
Experimental design: 1. Courtship frequency should be defined. Is it the number of courting males observed in 10 min as a fraction of total?
2. The results should be represented in a uniform manner. In Fig 1, the cVA responses were shown in courtship frequency and courtship index, while in Fig 2, only courtship index appeared. Then I noticed that the cVA response as courtship frequency was not reproduced in supplemental Fig 1, which should be carefully considered.

3. Fig 1b is confusing. The procedure for other figures should not be included.
Validity of the findings: no comment. described in "1. Basic Reporting".
Additional comments: I am curious whether cVA production is affected by the larval environment? Since chronic exposure to cVA changed the behavioral responses (Liu et al. 2011, Tachibana et al. 2015), it is possible that the effect in this report appeared through affecting cVA production. This is not crucial but would make this report more fruitful.


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: PRE-IMAGINAL CONDITIONING ALTERS ADULT SEX PHEROMONE RESPONSE IN DROSOPHILA
Review round: 1
Reviewer: 3

Output:
Basic reporting: No Comment
Experimental design: The manuscript “Larval imprinting alters adult sex pheromone response in Drosophila” by Everaerts et al. outlines exciting data that indicates that the effects of the sex pheromone cVA on adult fly behavior are more plastic than previously thought. Previous work suggested that the behavioral effects of cVA on adult fly mating behaviors are stereotypical and unconditional. However, this study indicates that the behavioral responses of males to cVA could be modulated by prior exposure to maternally-deposited cVA on eggs. The authors interpret these data to suggest that early exposure of individual male larvae to cVA and other maternal factors changes their biological response to cVA as adults via an imprinting-like mechanism. Although the molecular mechanism by which larval “imprinting” might affect adult mating behavior remains elusive, if true, these results could provide a power model for understanding how early sensory exposure could modulate adult complex behaviors. Below are some specific comments that I hope the authors will find useful:

1.	One conceptual issue with the proposed mechanistic model is that previous studies reported that the half-life of transferred cVA to females is very short. Typically, no cVA is detected in mated females 24h post-copulation. Yet, females will continue laying eggs for days after mating. If the data presented here are robust, it would suggest that the described mechanism would be only effective in modulating the behavior of some males but not most. What might be the ecological significance of such a mechanism for female fitness should be discussed.

2.	This report is not the first to suggest that pre-adult conditioning could affect adult specific behavior. One infamous example includes the report of Tully et al. (1994) about the retention of odor memories from larvae to adult flies. Yet, all attempts to replicate these findings have not been successful (e.g., Barron & Corbet 1999). The authors should use this example to warn their readers that the concept they introduce here, and their specific mechanistic interpretations of the data, are not congruent with what we think we know is happening during the extensive remodeling of the pupal nervous system in holometabolous insects.

3.	In lines 275 to 293, the authors discuss explanations for their observed phenotypic variability in behavioral response to cVA. While their arguments make sense, they seem to rely on some assumptions that may not hold. First, the authors assume that the variation that they see in amount of cVA on eggs and adult behavior are typical in the wild. However, these variations are likely not biologically relevant, as female flies readily re-mate before 10 days post-mating (reviewed in Singh et al 2002) and therefore 10 day-post-mating eggs are not likely to exist in nature.  Second, the explanation in lines 291 and 292 in lieu of the authors’ data (which outlines male behavior alone at 10 days post-mating) assumes that males alone control whether females will re-mate, which is not true.

4.	The authors assume that exposure to cVA and other maternally-transmitted factors in the larval stage is involved in the suppression of behavior in adult flies. However, their data indicates that synthetic cVA exposure does not rescue imprinting effects. Yet, synthetic cVA is sufficient to induce the adult behaviors they are focused on. They also note that the receptors for cVA are not present in larvae. Together, this suggests that perhaps cVA is not actually involved in the observed “imprinting” effect. Instead, other factors associated with the deposition of high cVA levels (which are also presumably removed via egg washing) somehow affect the adult behavioral response to cVA.

5.	Numerous studies have shown that male mate choices in Drosophila are the product of an interplay between stimulatory and inhibitory signals. Therefore, one possible cVA-independent model the authors should consider is that the observed effects are mediated by factors that suppress detection of stimulatory courtship signals rather than induce the detection of inhibitory signals such as cVA. Under this model, the larval “imprinting” process leads to a reduced perception and/or integration of stimulatory pheromonal signals, which could lead to the observed apparent increased sensitivity to cVA. Since the authors analyzed the CHC profiles of eggs, it would be useful to add these data to the paper, which would support or reject the hypothesis that other pheromone-like compounds are associated with high cVA maternal deposition.

6.	In line 172, the authors refer to “courtship frequency”, which is only defined in a figure legend, and not in the text. The authors should describe the details of all their behavioral measures in the methods section.

7.	The authors do not mention results related to Figure 1e until line 210, after discussing Figure 2. This is confusing and disrupts the overflow of the manuscript.
Validity of the findings: See above.
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: TUMOR-PREVENTING ACTIVITY OF ASPIRIN IN MULTIPLE CANCERS BASED ON BIOINFORMATIC ANALYSES
Review round: 1
Reviewer: 1

Output:
Basic reporting: fine as is.
Experimental design: Data sources are heterogenous and might have created bias. The authors should address this.
Validity of the findings: Data sources are heterogenous and might have created bias. The authors should address this.
Additional comments: I have enjoyed reading this paper. This is overall a well conducted bioinformatic study. This is very timely topic as we now characterize medications and tumors deeply to personalize prevention, treatment and management. There are a few issues.

The authors should discuss molecular pathological epidemiology (MPE) research. Using human populations, MPE can deeply study phenotypes of disease outcome such as cancer using molecular pathologic analyses, and link factors such as environment, diets, and aspirin to molecular pathology, augment causal relationships. It would be great to have detailed discussion on application of tumor biomarkers and cancer subtyping to MPE, and its impact on medicine and populations. You can see reviews on MPE in Gut 2011, Epidemiology 2016, Gut 2018, 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: TUMOR-PREVENTING ACTIVITY OF ASPIRIN IN MULTIPLE CANCERS BASED ON BIOINFORMATIC ANALYSES
Review round: 1
Reviewer: 2

Output:
Basic reporting: concise , well structured article.
Experimental design: rigorous investigation was performed using various bioinformatics tools.
Validity of the findings: no comments
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: TUMOR-PREVENTING ACTIVITY OF ASPIRIN IN MULTIPLE CANCERS BASED ON BIOINFORMATIC ANALYSES
Review round: 1
Reviewer: 3

Output:
Basic reporting: Article lacks an overview of relevant literature in the content of similar types of bioinformatics studies.

The discussion section is a long listing of results and a number of statements borrowed from literature that lack focus and a convincing analysis. I was lost as to what you are trying to prove and what you actually accomplished.

Minor issues
The abstract is loaded with jargon, especially in the methods part. This should be rewritten to be more accessible.
The writing is repetitive. The earlier sections of results are repeated in the discussion. This should be avoided.
Experimental design: The approach taken by the authors seems relatively naïve and the reported results seem rather preliminary in nature. There are a number of unexplained decisions that lead to likely incomplete/inadequate treatment of the topic and incompleteness/bias in the results including (but not limited to):
- Why did you use only DrugBank to annotate drug targets? – There are many other resources that should be use together with this database to annotate a more complete list of targets.
- Why did you use STRINGS, instead of a more reliable source, like mentha? How do you justify the 0.5 as the minimum score?
- How do you justify the assumption that PPIs that involve the aspirin targets would actually affect their partner proteins?
Validity of the findings: The results (enriched pathways, GO terms etc.) lack proper statistical analysis. The fact that a given term is enriched does not mean that this results in meaningful. This should be compared with a baseline to evaluate whether a similar results would be established for other drugs that are not recommended for treatment of cancer. Drug targets are a biased group of proteins and they are unlike a random set of proteins that you assume in your analysis.

The authors claim that “This method allows us to clearly map out aspirin-related DPTs and their associated genes to their biological pathways and clinical outcomes. Not only does this information contribute towards current knowledge of how aspirin prevents cancer, it also uncovers potential treatment targets, providing new directions for cancer therapeutics.” IMHO, this is not supported by the submitted manuscript. The authors generate mostly putative protein targets, few of them are in fact direct (given the use of STRINGS), they do not provide links to clinical outcomes – just speculate about such links, and finally I do not see how this provides new directions for therapeutics given that not a single new example of that was demonstrated by the authors.
Additional comments: This is a rather preliminary study that would require more work before future re-submission. The computational setup lacks depth and justification, statistical analysis is missing, and the authors made strong claims that in my view lack evidence.


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: TUMOR-PREVENTING ACTIVITY OF ASPIRIN IN MULTIPLE CANCERS BASED ON BIOINFORMATIC ANALYSES
Review round: 1
Reviewer: 4

Output:
Basic reporting: 1. The manuscript is written in clear and unambiguous, professional English.
2. The literature cited is satisfactory.
3. The article structure , figures and tables are professionally drafted.
4. The results and hypotheses projected in the study are satisfactory and self contained.
Experimental design: 1. The bioinformatic analyses described in the study has potential for further experiments to validate potential targets of Asprin action.
2. the research question is well designed. The authors have taken a bioinformatic approach to mine the existing data to hypothesize the role of asprin  in cancer biology.
3. The methods described are sufficient in context of the present study.
Validity of the findings: 1, the findings presented in the study may lead to further investigation in the mechanism of asprin in cancer biology. However, the data presented in the study is bioinformatic and needs further validation through experimental biology.
2. The data is statistically fine and conclusions of the study are well stated.
3. The data needs more experimental validation.
Additional comments: 1. Asprin has show to have some affects on melanoma and ovarian cancer. Did the authors have any data on these cancers? If so, please add data for the same.
2.the authors should describe more about the role of asprin in cancer metastasis.


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: TUMOR-PREVENTING ACTIVITY OF ASPIRIN IN MULTIPLE CANCERS BASED ON BIOINFORMATIC ANALYSES
Review round: 2
Reviewer: 1

Output:
Basic reporting: improved
Experimental design: imroved
Validity of the findings: improved
Additional comments: improved


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

Input:
Title: TUMOR-PREVENTING ACTIVITY OF ASPIRIN IN MULTIPLE CANCERS BASED ON BIOINFORMATIC ANALYSES
Review round: 2
Reviewer: 2

Output:
Basic reporting: Sufficient
English needs to be copyedited by a native speaker
Experimental design: Sufficient
Validity of the findings: Sufficient
Additional comments: English needs to be copyedited by a native speaker.


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: WIND-DRIVEN SPUME DROPLET PRODUCTION AND THE TRANSPORT OF PSEUDOMONAS SYRINGAE FROM AQUATIC ENVIRONMENTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The language used throughout is professional and meets the standards required to publish in the scientific literature. Unfortunately, a number of key topics are missing from the literature review and in those topics that are covered a number of key references are missing. The authors need to address this issue before this article can be published. Specific areas that need to be included are described in the attached PDF.
Experimental design: The experiment the authors describe is certainly novel and fully fits the aims and scope of the journal. Unfortunately, the description of the wind-wave flume used by the authors is not adequate making verification of the presented results impossible. Key experimental design details (replication etc.) are also missing. The authors need to address these issues before this article can be published. Specific areas that need to be included/expanded upon are described in the attached PDF.
Validity of the findings: Unfortunately, it is impossible to verify the robustness of the data given that key descriptions of the setup used and experimental design details are missing. It will only be possible to evaluate this when revisions to these sections have been made.
Additional comments: I would like to encourage the authors to spend some time revising their manuscript - their wind-wave flume is a useful addition to the tool-kit we have to investigate aerosolisation of bacteria from aquatic interfaces. Please see the attached PDF for more general 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: WIND-DRIVEN SPUME DROPLET PRODUCTION AND THE TRANSPORT OF PSEUDOMONAS SYRINGAE FROM AQUATIC ENVIRONMENTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Pass, the paper is well written and documented no issues here
Experimental design: Fail
I do not think that this design will produce an air-flow pattern that is comparable to natural situations. Furthermore the air velocity at the inlet will be higher than that farther downwind where it was measured since it is coming in through a small inlet and will spread and slow down as it moves into the large space. This has several implications.
First the wind speed at the water surface is likely larger than reported.
Second the assumption of a logrithmic boundary layer profile is likely not appropriate.
Third, the wind will decelerate away from the inlet and then increase again toward the outlet in a way that is not comparable to a wind over a natural water surface.
In order to address these issues additional measurements need to be made to deduce the velocity structure in the tank. Also some visualizations of smoke could shed some light on this. I dont believe that the streamlines revealed by this will support the analysis done and the extension to U10 but it has to be explored for the manuscript to be publishable.
Validity of the findings: Fail
This is primarily do to my serious issues with the experimental design.
Additional comments: Line 80 Why two different speeds given, there has been a number of papers that support the lower number.
Monahan and O’Muircheartaigh,
1986; Hanson and Phillips, 1999

Line 156, how were the particles sized if a heliocentric camera or collimnated light source were note used
Line 161, what was the air-water temperature difference
Line 272, this seems strange, any explanation?
Line 352, Should also cite Ortiz-Suslow et al, 2016 (Journal of Atmospheric Sciences, 73, 3975-3995) which has the most comprehensive droplet production measurements reported.


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: WIND-DRIVEN SPUME DROPLET PRODUCTION AND THE TRANSPORT OF PSEUDOMONAS SYRINGAE FROM AQUATIC ENVIRONMENTS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The paper is improved from the first version, I now think that only minor revisions are required.
Experimental design: The authors have addressed my concerns about experimental design in that they cite measurements that show that the flow is not accelerating in the domain over which they are sampling. However they make an obviously erroneous statement when they do so. To say that there are breaking waves and spray and that the flow is laminar is contradictory. There can be  no laminar (ie non-turbulent) flow in such conditions. I believe that they meant to say spatially uniform (or non-accelerating) flow. If the authors fix this error then the paper is publishable.
Validity of the findings: NA
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: WIND-DRIVEN SPUME DROPLET PRODUCTION AND THE TRANSPORT OF PSEUDOMONAS SYRINGAE FROM AQUATIC ENVIRONMENTS
Review round: 2
Reviewer: 2

Output:
Basic reporting: Review comments have been removed by the Editorial Office.  Reviewer 3  did not provide permission for their comments to be made public
Experimental design: Review comments have been removed by the Editorial Office.  Reviewer 3  did not provide permission for their comments to be made public
Validity of the findings: Review comments have been removed by the Editorial Office.  Reviewer 3  did not provide permission for their comments to be made public
Additional comments: Review comments have been removed by the Editorial Office.  Reviewer 3  did not provide permission for their comments to be made public


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: HIGH-THROUGHPUT METABARCODING REVEALS THE EFFECT OF PHYSICOCHEMICAL SOIL PROPERTIES ON SOIL AND LITTER BIODIVERSITY AND COMMUNITY TURNOVER ACROSS AMAZONIA
Review round: 1
Reviewer: 1

Output:
Basic reporting: Justify why you are asking question one. Why do you expect a different between the litter and soil layers?
Experimental design: Why not use a Procrustes analysis to evaluate the dissimilarity patterns (as estimated by the Jaccard) between the litter and soil layers?
Validity of the findings: The sampling was minimal when compared to the vastness of the Brazilian Amazon, but no sampling is perfect. Better care should be taken when discussing the results in the larger context of this entire region.
Additional comments: Line 29: “In contrast” to “By contrast”.

Lines 70-71 and 329-331: Bates at al. (2013, ISME J. 7: 652-659) also found pH drives soil protist diversity.

Lines 154-150: State chemistry used in the Illumina sequencing. State primers and their references. Ritter et al. (in review) should not be used as a reference as it is not published.

Lines 164-165: Justify clustering similarity value used.

Line 331: “dominant group” to “dominant eukaryotic group”.

Lines 310-313: Some studies would disagree that fungi are the dominant tropical eukaryotic group.

Figure 5: Use different point shapes to distinguish the different habitats. When printed in black-and-white, the colors all look the same.


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: HIGH-THROUGHPUT METABARCODING REVEALS THE EFFECT OF PHYSICOCHEMICAL SOIL PROPERTIES ON SOIL AND LITTER BIODIVERSITY AND COMMUNITY TURNOVER ACROSS AMAZONIA
Review round: 1
Reviewer: 2

Output:
Basic reporting: This paper describes a study on microbial prokaryotic and eukaryotic communities in soil and litter fractions, and their correlations with physico-chemical properties along the Amazon river in the Brazilian Amazonia. The authors use multivariate analyses and correlations between prokaryotic and eukaryotic OTU data tables and physical and chemical properties to investigate the main physico-chemical properties influencing the structure of these microbial communities in tropical forests.

The article is well written and well-structured with clear and unambiguous writing and professional English used throughout. The authors present clearly their objectives, methodology and results. Sufficient context is provided. However, I would suggest the authors stating clearly their hypotheses based on the previous research and adding some additional information in the methods that is notably missing.

All appropriate raw data is available (see comments on general comments to authors).

Figures are relevant to the content of the article, of good quality and appropriately described and labelled.
Experimental design: I consider that this article shows original primary research within the scope of PeerJ journal

The methodology is well described with sufficient detail to be reproducible by another researcher. It is appropriate for the questions showed in the paper. The research has been conducted to a high technical standard and in conformity with the prevailing ethical standards in the field. However, I consider that ‘soil’ and ‘litter’ should be appropriately described in section 2.1. There is a complete description of land uses and location of the plots, but it is not clear how the authors collected litter and soil substrates. Therefore, I strongly suggest describing this important sampling methodology.
Validity of the findings: The data are robust, statistically sound and controlled. Discussion is rather speculative as one important property (N content) is missing which would have improved the discussion of the manuscript towards the nutrient cycling issue. However, the paper shows important results that have been properly analysed and they worth its publication in PeerJ.

The conclusions lack some connection to the original questions investigated so I would suggest the authors re-writing this section including the conclusions linked to scientific questions.
Additional comments: I find that this paper is well written, well-structured and the methodology is appropriate for the questions raised by the authors. However, from my point of view, some important issues would need to be addressed before its publication (see comments below). Therefore, I suggest major revisions for its publication in PeerJ.

The research questions are well defined, but they still need to be well introduced to make them relevant and meaningful. The state of the art of the first question of the paper (differences between microbial communities’ structure and richness between soil and litter and their interactions with abiotic environmental properties) is not well defined as the main hypothesis regarding this question is not stated. What do the authors expect? This should be defined based on previous bibliography.

Additionally, important methodological information is missing: litter and soil description and sampling (which is particularly important for this paper). Therefore, I strongly recommend to describe properly what the authors understand by ´litter´ and ´soil´ fractions. What is the depth?, was it the same for the different land uses? Is ´litter´ the plant debris? Does it include woody/root debris?

Generally, the R script is clear and easy to follow but has some important issues that would need to be addressed, particularly in the second part of the script that cannot be run:
•	Compilation to word document did not work so I followed the script.
•	The ‘install.packages’ command is missing for the package called ‘splancs’
•	The files provided have a different name to the filenames used in the script (e.g. 16S_all.csv). I suggest changing the names in the script (to e.g. peerj-26029-16S_all).
•	A folder ‘output’ would need to be created to save output files but it is not described in the script.
•	Line 117, not quite sure what you want to do here: OTUSbiol <- select(dat, Locality:OTUS_18SS), there is not any column with that name in ‘dat’ dataframe.
•	Line 350: change ‘summary(s18l.nmds)’ to ‘summary(s18.nmds)’
•	Line 438: Second hypothesis: I was not able to follow this part of the script as the ‘mice’ function is applied to dat, but the last reference to ‘dat’ is:
         dat <- read.csv("peerj-26029-metadata.csv")
         dat <- data.frame(dat[,1:7])
         names(dat) <- capitalize(names(dat))
         so it is not possible to apply mice as it is in the script: tempData <- mice(dat[1:39,8:27], m=5, maxit=50, meth='pmm')
•	Hereafter, the script cannot be run (from line 438). So I strongly suggest the authors revising the script and running it again to be sure it can be run in other computers.

I suggest the authors reading the paper McMurdie PJ, Holmes S. 2014. Waste Not, Want Not: Why Rarefying Microbiome Data Is Inadmissible. PLOS Computational Biology 10(4): e1003531 for future research and I would suggest the authors not using rarefaction in the future and particularly for this paper as they are using presence/absence matrices to do their analysis. A priori, I would think rarefaction is not needed if working with presence/absence and with richness indexes. Another important question, why do the authors use presence/absence data? it should be justified in the text.

Discussion is well written and somewhat speculative in the nutrient cycling aspect. However, PeerJ welcomes speculative discussions if they are appropriately discussed as it is here. The nutrient cycling discussion would have been strongly supported if Nitrogen would have been measured to estimate C:N rates and discuss in depth the nutrient cycling and stoichiometry.

Some more detailed details are showed below:

Line 31: The aims of the work are notably missing in the abstract.

Line 76: Porazinska et al. 2012 showed differences in taxonomic composition for nematodes, it would be good to specify it.

Line 96: ‘Physio-chemical’ should be corrected to ‘physico-chemical’

Line 101: It is not clear what the authors expect from these data in contrast with the antecedent literature. I would suggest specifying the hypothesis for the first question.

Line 133: What do the authors mean by ‘determining the physicochemical and nutrient profiles of the first 5 cm’? Did they measure ‘along the profile from surface to 5 cm’? I understand samples were taken from the first 5 cm, so I suggest rewriting this sentence to ‘determining the physicochemical and nutrient properties of the first 5 cm’

Line 145: I suggest using ‘coarse’ instead of ‘thick’ when referring to sand (line 184 too).

Line 198: Apart from the ‘envfit’, another possible approach would have been to perform a Permutation Analysis of Variance (PERMANOVA test) to investigate if these factors do have a significant effect on the structure of the communities.

Line 206: I suggest changing ‘correlates’ to ‘correlated’.

Line 236: Here the authors are showing the adj. R2 whilst the R is showed in the figure caption. It is confusing, and I suggest showing only one value (I suggest adj. R2).

Line 247: This might be due to the rarefaction, it should be discuss in the discussion section.

Line 270: I suggest changing ‘soil properties’ to ‘soil/litter properties’.

Lines 279 and 280: Change ‘physic’ to ‘physico’

Line 302: A comma should be deleted in the reference Delgado-Baquerizo.

Line 351: I suggest changing ‘puzzling’ to ´unexpected´.

Line 370: I would suggest changing ‘diversity’ to ‘richness’.

Tables:

Table 1: Caption: Change OUT to OTU.
Table 1: ‘As the organic carbon content and pH are important variables to soil biota, we use them as independent variables.’ This is not explained in the text and should be specified in the Materials and Methods section.

Figures:

Figure 2. I suggest adding the regression fitness coefficients to the figures.
Fig. 3. I would delete ‘in Amazonian samples’ in the figure caption title as only Amazonian samples are showed in this paper.
Figure S4. In figure caption, I suggest changing ‘Blues circle are soils samples and red are litter samples. The sizes…’ to ‘Blue circles represent soil samples and red represent litter samples. The size…’.
There is not any figure S3, so I suggest numbering S4 as S3 and in the text.


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: HIGH-THROUGHPUT METABARCODING REVEALS THE EFFECT OF PHYSICOCHEMICAL SOIL PROPERTIES ON SOIL AND LITTER BIODIVERSITY AND COMMUNITY TURNOVER ACROSS AMAZONIA
Review round: 1
Reviewer: 3

Output:
Basic reporting: The report is well written.

Some references are missing (check attached file).

The Raw data (fastq files) are not publicly available, they should be submitted to a public database like SRA.
Experimental design: Successfully performed.
Validity of the findings: The main problem I have found in this study is that richness is assumed as diversity. The relative abundance of each OTU is not taken into account, nor is evenness taken into account when discussing the composition of the community.

Some assumptions may be wrong because of the problem discussed above.

Some data in the text are not supported in any table or figure (lines 307-311 and line 320).

As for the rest of the text, I find it an interesting and well-reported study.
Additional comments: I suggest that the authors conduct the study and comparisons taking into account the relative abundance of each OTU when comparing the composition of the different communities.


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: HIGH-THROUGHPUT METABARCODING REVEALS THE EFFECT OF PHYSICOCHEMICAL SOIL PROPERTIES ON SOIL AND LITTER BIODIVERSITY AND COMMUNITY TURNOVER ACROSS AMAZONIA
Review round: 2
Reviewer: 1

Output:
Basic reporting: Now good.
Experimental design: Now good.
Validity of the findings: Now good.
Additional comments: In this revision, I feel that authors have successfully and fully answered my previous comments.