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: ASSOCIATIONS BETWEEN PSYCHOMETRICALLY ASSESSED LIFE HISTORY STRATEGY AND DAILY BEHAVIOR: DATA FROM THE ELECTRONICALLY ACTIVATED RECORDER (EAR)
Review round: 1
Reviewer: 1

Output:
Basic reporting: The standard of reporting is generally very full and clear. However, I do confess that I find the inclusion of the HEXACO analyses confusing. I can grasp the idea of a study to see whether life history strategy constructs predict quotidian behaviours. Then I can grasp that there are three different measures of life history strategy, that these do not correlate well with one another, and that hence you need to look at each different life history strategy measure in relation to each behaviour. But then introducing six *other* constructs, that seem to me to be related to a different set of questions, and to relate each of those to every behaviour – it causes huge issues of multiple testing, and to my mind it starts to make the whole paper incoherent. Are the HEXACO dimensions supposed to be sub-constructs of life history strategy (this is how they are often discussed)? Or are they alternative predictors when life history strategy does not work (as table 5 implies). This just doesn’t make any clear sense to me, and it overlaps with other papers already published by the author. I would advise taking the HEXACO stuff right out in order to be clearer about the rationale and interpretation of the life history strategy material.
Experimental design: I really want to commend the author on his interest in quotidian behaviour, and his willingness to go the long hard road of a behavioural study using the EAR. Relating quotidian behaviour to personality or psychometric constructs as usually used in psychology is a great objective and this data set is a non-trivial achievement. I also want to commend the use of the Bayesian stats, and going right down to the raw behavioural outcomes rather than aggregating.

Despite these strengths, I have some major concerns about the design.

1.	There seems to me to be a huge problem of multiple testing, which the Bayesian stats do nothing to address. You get enough behaviours, and test the probability of occurrence of each of them with each of several psychometric predictors, and sure enough, you find some positive associations stronger than chance. They are not in general the ones you predicted, and not the same ones for the three measures of life-history strategy, and there are not very many of them. We need some sense of how many associations you would get by chance with that degree of multiple testing anyway. Relatedly, no very informative measure of effect size, like R2 or proportionate reduction in variance, is offered, so we don’t know if knowing life-history strategy dramatically or only marginally improves our ability to predict behaviour. In effect, we need a null model and a sense of to what extent life history strategy measures allow better prediction than the null model. There are several ways to implement this within the author’s framework. One thing I would suggest is to scramble the dataset. That is, randomly re-assign all the life history scores to different people. Then rerun the analyses. Indeed the beauty of working in R is that you can do this many times. I think we need an overall sense of how much better we do with real measures of life-history strategy than with random data. I’d like to see this quantified – I think the answer may well be not much. This often happens in psychometric research. People predict lots of associations, find a few of them, and then present the results as partial support for the predictive framework. But it is not at all obvious that it is even partial support.

2.	 Another problem that strikes me is that the life history strategy measures are of two categorically distinct kinds. The AHLB is a separate source of information from the EAR recordings and diaries. Thus, correlations between it and the recordings and diaries do tell us something. The CAQ measures, as I understand them, were made by raters *using* the EAR recordings and diaries. Thus, they are not independent of those recordings and diaries. Any correlation between the recordings/diaries and the CAQ thus really just tell us how the raters did their job – they used information in the EAR data set to produce the CAQ. Correlations should be expected. In fact, it’s odd they are so weak. For me this is really problematic. Basically you are using a human-created qualitative summary of a set of data to try to predict what is in that data – so what does that tell us about the actual participants? I don’t have a solution to this, except that for me the CAQ stuff suffers from a kind of circularity, and only the ALHB stuff is telling us anything about the relationship between the life history construct and quotidian behaviour.
Validity of the findings: I think you can tell from my comments under experimental design what my concerns about the validity of the findings are. I don’t quite know what implication the author intends. For example, there are two measures of life-history strategy here that are supposed to be measuring the same thing: the CAQ overall, and the ALHB, and they are basically uncorrelated (I really had to dig to find this information). Not only that but they have different patterns of association with other constructs like the HEXACO. What does this mean for the whole construct? To my mind it renders it problematic, and yet there is no critical discussion of the utility of the construct.

Then there is the fact that most of the predicted associations don’t materialise with any of the measures, and no association appears with all of them (and see experimental design above for my concern about circularity with the CAQ score anyway). There is even one in the opposite direction. So is it not time to start doubting the utility of the slow life history construct? What would it take for the author to conclude that the construct was not useful in predicting behaviour, or is not really measuring a thing?

In short, I don’t quite know what hypothesis is under test, and hence don’t know what answer comes back. Maybe the author could consider posing himself a more sharply defined question, such as: ‘How well does the Arizona Life History Battery score allow us to predict quotidian behaviour?’. Then, we could come up with clear quantitative answer: we can reduce our uncertainty by x% by knowing the AHLB score compared to not knowing the AHLB score. There are a couple of ways you could do this. 1. The data randomization strategy described in Experimental Design; or 2. Calculating something like the proportional reduction in variance (PRV) due to ALHB for each behaviour, and then averaging this across behaviours (see e.g. Nakagawa, S. & Schielzeth, H. 2013. A general and simple method for obtaining R2 from generalized linear mixed-effects models. Methods Ecol. Evol. 4, 133–142).
Additional comments: The author knows me, I like his work, and so let me say I am sorry for giving him a challenging review. He will no doubt come back at me if he disagrees with my characterization. I have gone out of my way to commend his interest in measuring quotidian behaviour, and the use of the EAR method in particular. It’s a useful data set, but I think the paper would have more impact if conceptually tidied up, streamlined, and answering a clearer, sharper non-circular problem.


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: ASSOCIATIONS BETWEEN PSYCHOMETRICALLY ASSESSED LIFE HISTORY STRATEGY AND DAILY BEHAVIOR: DATA FROM THE ELECTRONICALLY ACTIVATED RECORDER (EAR)
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper is clear and well-written.

There are a few spots that should be corrected:

-“enrolled at” is repeated twice in the participants subsection.
-“vary” should be “very” under “California Adult Q-sort (CAQ) life history strategy scoring” section
Experimental design: The design is rigorous with multiple measures to assess LHS. The Methods are described in detail.
Validity of the findings: The psychometric approach to assessing LHS has been mostly deficient in looking at observations of behavior (ethograms) rather than only reported behavior. This paper is helpful filling that gap and doing so with some diversity of measures of LH strategy.
Additional comments: My bottom line is that I think the paper is excellent and should be accepted for publication—without much revision. It makes an important contribution in the study of how measures of LHS relate to daily behaviors. The psychometric approach to LHS has been deficient in looking at observations of behavior (ethograms) rather than only reported behavior. This paper is helpful filling that gap and doing so with some diversity of measures of LH strategy.

Paul R. Gladden, Ph.D.
Interim Department Chair
Associate Professor of Psychology
Department of Psychology and Criminal Justice
Middle Georgia State University
Macon, GA
paul.gladden@mga.edu


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

Input:
Title: ASSOCIATIONS BETWEEN PSYCHOMETRICALLY ASSESSED LIFE HISTORY STRATEGY AND DAILY BEHAVIOR: DATA FROM THE ELECTRONICALLY ACTIVATED RECORDER (EAR)
Review round: 2
Reviewer: 1

Output:
Basic reporting: The standard of reporting is very high.
Experimental design: The study is now well-designed, once the various extra measures of the earlier version have been cleared away.
Validity of the findings: I think the findings are valid and we can have some confidence in them, albeit that they are mainly neutral associations.
Additional comments: I'd like to congratulate the author on the revisions. It took some wielding of the scalpel, but I think the resulting manuscript is much clearer and sounder.


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: SOCIO-ECONOMIC FACTORS AND MANAGEMENT REGIMES AS DRIVERS OF TREE COVER CHANGE IN NEPAL
Review round: 1
Reviewer: 1

Output:
Basic reporting: This article is well written. Background information and literature are well explained and covered. Figure 1 needs north arrows and scale bars. Research questions are clearly addressed. Table 2 is not self-explainable for the variables of Ncfug, Ppop, and Rlength.
Experimental design: I'm a little concerned about the use of global forest cover data for local use though many studies use this approach. It will be helpful to directly or indirectly valid partial data with locally derived forest cover data. The manuscript mentioned 'spatial accuracy'. Further explanations would be better.
Validity of the findings: The validity of the findings depends on the accuracy of the data sources, including forest cover data. Please refer to my previous comments in box 2. The statistically methods seem no problems.
Additional comments: I have one major suggestion: the 2015 data is now available and it would be better to include the 2015 data into the 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: SOCIO-ECONOMIC FACTORS AND MANAGEMENT REGIMES AS DRIVERS OF TREE COVER CHANGE IN NEPAL
Review round: 1
Reviewer: 2

Output:
Basic reporting: 1. Hundreds of models have been created to access the social-economic drivers (underlying forces) of deforestation on the sub-national and national scales around the world (Angelsen and Kaimowitz, 1998). A paragraph about background and introduction should be indicated with a summary of modeling methods and using data.
Experimental design: 2. Angelsen and Kaimowitz reported the existence of more than 115 different variables had been used to explain deforestation. Prior studies have identified several vital underlying forces related to deforestation: forest logging, timber price, forest land accessibility, soil suitability for agriculture and so on. Besides, political aspects, like the creation of conservation territories may also impede deforestation (Muller et al., 2012, Chomitz and Gary, 1996, Rosa et al., 2013). Why are these critical drivers not considered in this study?
Validity of the findings: 3. In this study, the author(s) disaggregated tree cover (both extent and change) into five physiographic zones and 75 districts. Why the author applied the regression analysis only on an aggregated level.
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: SOCIO-ECONOMIC FACTORS AND MANAGEMENT REGIMES AS DRIVERS OF TREE COVER CHANGE IN NEPAL
Review round: 1
Reviewer: 3

Output:
Basic reporting: Generally well-written, although grammar requires checking for minor revision. For example, Abstract: “in response to a massive deforestation” (L14-15); “with a huge spatial and temporal variations” (L21-22); and so on throughout.

The Introduction is interesting and provides solid context and motivation for the work, which is of global interest. However, here and/or in Discussion, I miss some global context for the success or otherwise of community-based management (CBFM) schemes. What is the (global) state of knowledge on the success of devolved forest management, especially in countries most similar to Nepal?

The structure of the article is sound. There are no original data that could be shared with the reader, and the sources that are used appear to be well referenced (although I have not checked whether every dataset could indeed be assessed via the references).

Aims are clearly stated, except that “identify policy actions needed to stem deforestation and forest degradation” does not seem to be directly addressed in subsequent sections: the policy-relevant intervention being tested here is the presence or absence of CBFM, and its correlation with rates of tree cover change; but other policy action are not assessed as far as I can tell, nor is forest degradation (as opposed to clearance) assessed directly. I suggest rewording to be more specific to what is being investigated.
Experimental design: The authors construct a multivariate model investigating the response of net change in tree cover to multiple independent variables (15 in total I think - Table 1). Due to the spatially aggregated nature of some of the variables, this analysis is conducted across N=75 districts.

The authors test for collinearity (Fig S1) but have not acted on those findings, apparently including all 15 variables and performing model selection according to AIC. I suggest that redundancy in the predictor set could be reduced, by considering both collinearity and by being more targeted in terms of the relevant units for each hypothesized effect.

For example, the response variable is *area* of tree cover change, which is presumably sensitive to district size (or at least forest extent at t0). In some cases, the authors have included both the raw numbers as an independent variable, and then also another version that is scaled in some way by area: for example, “number of community forest groups” and also the “percentage of major vegetation area … covered by community forests” (the model with the lower AIC retains the former, but not the latter). Similarly, population is included in several ways: as total district population in 2001, as the density of people outside protected areas, and as the number people below the poverty threshold.

Might the result be different if the response variable was the *proportion* of forest that was lost or gained, modelled against only those predictors that are appropriately scaled by area? Following the authors stated concerns regarding the potentially confounding effects of protected areas (L217-220), population density excludes such sites from the calculation. Similarly, I would expect the same area-based correction to apply to the number of people living below the poverty threshold (this variable is returned in the lowest-AIC model, but is currently the absolute number of people, correlating positively with the absolute area of forest change).

The authors are best-placed to decide on these matters, but I urge them to consider carefully the extent to which area-effects and collinearity might impact the inferred importance of certain variables.

In a separate analysis, the authors compare tree loss and gain at different distances from the roads. The result here are interesting (Fig 3a), however the description of methods is too brief to know exactly how these calculations were done (L231-233). Similarly, very brief methods (L233-234) accompany a temporal analysis of fire incidence and tree cover loss, which are highly correlated (Fig 3bc). It would be interesting to discuss the causes of the fires – are these deliberately set by people, to clear the vegetation? If so, is the fire incidence higher or lower under CBFM? Or are people in CBFM areas more likely to put out a naturally ignited fire? Might the multivariate model therefore include interaction terms? It is difficult to tell much here from the cross-correlations (Fig S1): the number of fires is correlated positively with the number of community based groups, but this could be due to bigger districts having both more groups and more fires than smaller districts. But then fire is negatively correlated with total population and with the number of poor people. As above, correcting according to appropriate area measurements might offer some insight.
Validity of the findings: The authors should be careful when implying causality from their current analysis, given the redundancy in variables and potentially confounding area-effects. And it would be useful if effect sizes (rather than just p-values) were discussed. For example, what impact does a unit change of CBFM (e.g. an extra group or an extra % of coverage) have on the net change in forest cover, and how does this compare to the other variables in the model? Also, were there other ‘top models’ besides the one with the lowest AIC? E.g. AIC within delta 4 of the top model?

In terms of guiding policy on the conservation of forests for biodiversity, ecosystem functioning and services, the distinction between natural forest and plantation forest should be dealt with more directly, in discussion if not in the analysis. The Hansen data do not distinguish between trees in plantations and natural forests that have been conserved or are regenerating, and as noted in the Discussion (L312-313), the community forests are often a mix of both.
Additional comments: Are different forest types more or less prone to deforestation (e.g. via grazing or fire) - could this be factored into the analysis by overlaying the land cover map with the Hansen data? And/or using physiographic region as a random grouping variable in a mixed-effects model? I offer this only as a suggestion/question, not as a criticism of the current work.


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

Input:
Title: SOCIO-ECONOMIC FACTORS AND MANAGEMENT REGIMES AS DRIVERS OF TREE COVER CHANGE IN NEPAL
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have made improvements to their basic reporting. In particular, I appreciate the additional introductory text on CBFM. The manuscript would still benefit from proof-reading for minor grammatical errors
Experimental design: The authors have improved their experimental design by reducing collinearity among predictors, and by analyzing area-corrected response terms. In my opinion, the results are more robust as a result, and it is encouraging to see that CBFM measures remain important. Some of the predictors, however, remain sensitive to area, so that, for example, higher fire incidence could signal either more fires per unit area, or a larger district, or both. I believe that this remains a problem / might explain some of the stranger results (e.g. fires correlating positively with forest gain; number of user groups correlating negatively with both loss and gain of forest). Please consider the following [alternatives] and justify where and why the uncorrected variables are more meaningful predictors.

- Number of community forest user groups [Mean area covered by a user group]
- Total population [I think this is redundant, given Pdensity]
- Absolute number of poor people [ditto, given Ppopdensity]
- Total number of livestock [Mean livestock per person, interacting with Pdensity]
- Total number of households using fuelwood [% of households, interacting with Pdensity]
- Number of migrants [Mean migrants per unit area]
- Total number of fire incidence [Fire incidence per km per year]. Were fire data (MODIS) clipped to the forest extent? This might increase relevance
- Total length of roads. The unit here is given as "Km/100km" - what does this mean?

I see that (maybe in response to another reviewer's comment?), the authors no longer look at net change in forest, but instead analyse only gain and loss separately. Personally I think this is a shame, though the disaggregated results are useful too. Could proportion change, relative to the baseline, be reinstated? i.e. three columns in Table 2: gain, loss, net
Validity of the findings: Thank you for the clarifications and more nuanced interpretation of results. I would still like to see effect sizes described in the text, not just p-values - I think this is important for interpretation of how much difference CBFM potential makes. Also were other models close to the 'best models' according to AIC (e.g. < delta 4)?
Additional comments: Many thanks for the clear and detailed rebuttal


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: GENOME-WIDE CHARACTERIZATION AND EXPRESSION ANALYSIS OF GRAS GENE FAMILY IN PEPPER (CAPSICUM ANNUUM L.)
Review round: 1
Reviewer: 1

Output:
Basic reporting: This article deals with the identification and characterization of GRAS gene family in chili pepper (Capsicum annuum L.). In general, the article is clear, with sufficient field background cited literature, well-structured and organized, with adequate support materials (figures, tables and additional tables), and with interesting and relevant results about this gene family. However, some writing minor mistakes were detected and marked in the text and in References.
Experimental design: Experimental design of this study is considered adequate, with a well defined question and appropriate experimental approach to answer it. This research is considered as well performed and with high technical standard. However, a just one possible weak part is that regarding the qRT-PCR expression analysis using actin as reference gene, because very often three reference genes are included for this kind of analysis due to some large variation of expression levels of them, as it has been particularly reported for actin gene in chili pepper considered as the least stable reference gene (see Wan et al., Biochem. Biophys. Res. Commun. 416:24-30 (2011).
Validity of the findings: In general, the overall analyses and results are very interesting and will be certainly of great value for the knowledge of GRAS gene family in chili pepper, which will be to encourage deeply research on the diverse functions of these genes.
Additional comments: Please attend all the marked corrections and observations indicated in the text of the attached file, following carefully the Instructions to Authors of this journal.


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: GENOME-WIDE CHARACTERIZATION AND EXPRESSION ANALYSIS OF GRAS GENE FAMILY IN PEPPER (CAPSICUM ANNUUM L.)
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall, the article is well written and well presented. The language at some sentences can be improved for clarity e.g. lines 9, 145, 170, 179, 271, 280, 359.
Experimental design: The article presents the analyses of GRAS gene family in pepper. Most of the manuscript is descriptive with different bioinformatic analyses of the GRAS genes.

Major comment:
- The rational of analyzing GRAS in pepper is unclear. GRAS family has been characterized in 30 plant species (lines 39-41), and authors do not discuss what's different in pepper GRAS genes compared to their orthologs in other species. I recommend that authors strengthen rational of their analyses and discuss the new insights and knowledge-gap that is achieved by their manuscript.

Minor comments:
- Abstract line 19: "...play vital roles in..." is too strong a claim. Expression does not imply a vital role. It should be "...may be implicated in...", or something to that effect.

- Line 133-135: How was the RPKM values obtained? If it was from the original published study, it should be clearly mentioned.

- Line 187-190: Are some of the GRAS paralogs originated, from whole genome duplications in plants? No evidence is presented for this.

- Line 264-265: Have authors looked for evidence that these genes are pseudogenes?
Validity of the findings: Findings may only be useful for a limited set of researchers.
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: GENOME-WIDE CHARACTERIZATION AND EXPRESSION ANALYSIS OF GRAS GENE FAMILY IN PEPPER (CAPSICUM ANNUUM L.)
Review round: 1
Reviewer: 3

Output:
Basic reporting: While the paper conveys the scientific message, it needs grammatical editing. The introduction is not coherent and contains too much information not pertaining to the study.
Experimental design: The authors should clarify how their pipeline is different than the previously published papers. It would be helpful to see novelty rather than repeating template bioinformatics pipeline on different TF families or new plant varieties.
Validity of the findings: Please explain why use (only) these two cultivars of capsicum and using Arabidopsis to compare instead of some other close relative?

I think the authors and the paper would reach a broader audience and benefit more if they can include some more TF families in this study. Especially since most of the work is bioinformatics analysis, I strongly urge expanding the study to include couple other important transcription factors or at the very least include few other species or cultivars of capsicum.
Additional comments: Minor:
How many samples were used for figure 2?

Why do authors cite papers in the results section? They can relate their findings to previous literature in the discussion.

Why did the authors choose the “The length of all hits out of the range from 350 to 820 aa was rejected.”


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: GENOME-WIDE CHARACTERIZATION AND EXPRESSION ANALYSIS OF GRAS GENE FAMILY IN PEPPER (CAPSICUM ANNUUM L.)
Review round: 2
Reviewer: 1

Output:
Basic reporting: Authors attended the comments and observations made by the reviewers.
Experimental design: Authors attended the comments and observations made by the reviewers.
Validity of the findings: Authors attended the comments and observations made by the reviewers.
Additional comments: Authors attended the comments and observations made by the reviewers.


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: GENOME-WIDE CHARACTERIZATION AND EXPRESSION ANALYSIS OF GRAS GENE FAMILY IN PEPPER (CAPSICUM ANNUUM L.)
Review round: 2
Reviewer: 2

Output:
Basic reporting: The manuscript is much improved compared to the first submission.
Experimental design: No comments.
Validity of the findings: The scope is improved with additional analyses and data. Although this will still be only a little advance in the field without much insights.
Additional comments: The authors have satisfactorily answered my 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: GENOME-WIDE CHARACTERIZATION AND EXPRESSION ANALYSIS OF GRAS GENE FAMILY IN PEPPER (CAPSICUM ANNUUM L.)
Review round: 2
Reviewer: 3

Output:
Basic reporting: N/A
Experimental design: N/A
Validity of the findings: N/A
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: EXOSOMES IN CANCER: SMALL VESICULAR TRANSPORTERS FOR CANCER PROGRESSION AND METASTASIS, BIOMARKERS IN CANCER THERAPEUTICS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The review by Atefe Abek and colleagues is a comprehensive attempt to describe the multifaceted roles of microvesicles, exosomes, and microparticles in the carcinogenesis process. The authors cover a vast array of reports that have described the roles of these tiny vesicles in cancer progression, metastasis and drug resistance. The article is supported by a comprehensive list of updated references. The 5 figures are quite high quality and capture the essence of the exosomal signaling related to cancer. The table is very comprehensive and covers the subject in its entirety.

Specific comments:

The legends to the figure can be enhanced. This would make the figures self-explanatory

There are several instances where the authors have mixed up the tense which should be checked and corrected. For example the use of had is misplaced in this article

Typos should be checked and corrected
Experimental design: The review is very comprehensive and well designed
Validity of the findings: The article text is supported by updated references
Additional comments: The review by Atefe Abek and colleagues is a comprehensive attempt to describe the multifaceted roles of microvesicles, exosomes, and microparticles in the carcinogenesis process. The authors cover a vast array of reports that have described the roles of these tiny vesicles in cancer progression, metastasis and drug resistance. The article is supported by a comprehensive list of updated references. The 5 figures are quite high quality and capture the essence of the exosomal signaling related to cancer. The table is very comprehensive and covers the subject in its entirety.

Specific comments:

The legends to the figure can be enhanced. This would make the figures self-explanatory

There are several instances where the authors have mixed up the tense which should be checked and corrected. For example the use of had is misplaced in this article

Typos should be checked and corrected


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: EXOSOMES IN CANCER: SMALL VESICULAR TRANSPORTERS FOR CANCER PROGRESSION AND METASTASIS, BIOMARKERS IN CANCER THERAPEUTICS
Review round: 1
Reviewer: 2

Output:
Basic reporting: I think this paper contains a serious concern regarding the paper which they have cited. For instance, some of the paper, which they have cited, have used ExoQuck, which is the commercially available kit for isolation of "exosome" with contamination of other soluble proteins.
Authors should exclude these kinds of paper, which are not able to provide the evidence that each paper really worked on the exosome or not.
Experimental design: No comment on this. This paper is Review paper and there is no new finding based on the experiment.
Validity of the findings: No comment on this. This paper is Review paper and there is no new finding based on the experiment.
Additional comments: Overall, this manuscript was well written regarding the roles of the exosome in cancer development, however, some of the content of some of the topic is a little superficial. For instance, "6. Exosomes Isolation and Analysis" are critical for exosome research, and there are huge issues to be solved for this. Authors should describe the pros and cons of each method and should mention to the reader that commercially available kit has some limitation for the analysis of exosome research. In addition, as I wrote in the above, the paper, which authors have cited, is not appropriate for me. For instance, when they have mentioned about pre-metastatic niche, they have cited Khalyfa et al rather than the following paper which showed the evidence regarding the contribution of exosome in pre-metastatic niche formation firstly in the world. Authors should check all of the references again and cite the paper which has shown the things firstly in that research field or follow the context of their manuscript.

Peinado H, Alečković M, Lavotshkin S, Matei I, Costa-Silva B, Moreno-Bueno G,
Hergueta-Redondo M, Williams C, García-Santos G, Ghajar C, Nitadori-Hoshino A,
Hoffman C, Badal K, Garcia BA, Callahan MK, Yuan J, Martins VR, Skog J, Kaplan
RN, Brady MS, Wolchok JD, Chapman PB, Kang Y, Bromberg J, Lyden D. Melanoma
exosomes educate bone marrow progenitor cells toward a pro-metastatic phenotype
through MET. Nat Med. 2012 Jun;18(6):883-91. doi: 10.1038/nm.2753.


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: DACCOR–DETECTION, CHARACTERIZATION, AND RECONSTRUCTION OF REPETITIVE REGIONS IN BACTERIAL GENOMES
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is very well written. Just a couple of typos:

1. Table 1. Commas missing in false negatives row.

2. Table 2. Max length of repetitive regions for E. coli should have a comma instead of period.
Experimental design: 3. De novo assembly is almost completely ignored throughout the manuscript, but is one obvious way of reconstructing a genome sequence from reads. This should be discussed because it is the only viable option where a reference genome is not available, or where one cannot be sure that the reference is close enough to the reads to use a reference-based method. For example, “any one E. coli contains less than 10 % of the total number of E. coli genes in the E. coli pan-genome” (https://www.ncbi.nlm.nih.gov/pubmed/25722247).

I think it is important to compare DACCOR against a state of the art assembler, ideally SPAdes because it is currently the most popular for bacteria genomes. Show how well SPAdes reconstructs the rRNA genes compared to DACCOR and EAGER, and add the results to the end of the results section on page 6. If DACCOR is as good as advertised, then it should do better than SPAdes.

4. A few details need adding for reproducibility:
* All accession IDs for the genomes and reads used.
* Version numbers of all software used.
* Options used for all software - if it was the defaults then still state it.
* Any scripts written to help produce the results should be released, eg on github.
* How was the run time measured and on what type of machine?

5. Can the authors justify why it is ok to take VMatch as the truth (lines 144-148)? Is it guaranteed to find every repeat?

6. I tried out DACCOR and VMatch on a toy made up FASTA file that had repeats with a few SNPs and indel differences. VMatch can handle indels in its matches, but it appears DACCOR cannot. Repeats reported by DACCOR were broken where I put an indel, eg two copies of a sequence with the only difference being a single nucleotide indel in the middle. Ultimately I don’t think this matters to the overall method of DACCOR and the quality of the results, but could it explain some of the false negatives in Table 1? In any case, I think it would be good to clarify that allowing “mismatches” when running DACCOR really means SNPs only, not indels.
Validity of the findings: No comment
Additional comments: The manuscript is clearly written, and DACCOR looks like a useful tool for the community. The software looks well engineered and even appears to have unit tests.

My only other comments relate to the software:

7. Make a versioned release on github, corresponding to the current version (0.0.1) of the code.

8. Include the JAR file in each release, to save the user compiling (eg like Picard has). I had issues compiling on Ubuntu Zesty. gradle build returned the error:
java: symbol lookup error: /usr/lib/jni/libnative-platform-curses.so: undefined symbol: tgetent

I expect the cause was this known bug:
https://bugs.launchpad.net/ubuntu/+source/libnative-platform-java/+bug/1683761
but I didn’t pursue it further.

To be clear: this is not a fault with the DACCOR code, but a problem with that version of Ubuntu. However, releasing a JAR file should solve this.

I had no problems compiling the software on Ubuntu Xenial. I did not test on a Mac (or WIndows!).


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: DACCOR–DETECTION, CHARACTERIZATION, AND RECONSTRUCTION OF REPETITIVE REGIONS IN BACTERIAL GENOMES
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is well written and organized. However, the introduction is sometimes difficult to follow for people not coming from the bacterial genome field and the subject and the aim of the project after the first read of the introduction is not entirely clear. With respect to the wide scope of the journal this needs to be improved. The description of the method to reconstruct repetitive regions, the results and the discussion are generally of good quality but need at some points improvements (see below in the section “Comments for the author”). The figures are relevant to the content of the text and understandable.
Experimental design: No comment here. Please see line-by-line remarks in the section “Comments for the author”.
Validity of the findings: No comment here. Please see line-by-line remarks in the section “Comments for the author”.
Additional comments: 1) Introduction

Line 23
The term genome reconstruction needs to be clearly defined. From the context it seems to me like reference based genome assembly but I might be wrong. It is also highly recommended to make clear, that this is all in the field of bacterial genomes at a very early point. Why do you pick especially BWA from the dozens of mappers? Is it necessary to this very one.

33ff
The point of the last two sentences of the first paragraph is unclear.  Filtering low quality mappings is no problem – it is a unavoidable step.

37
Please change “role in the genome” to “role in many genomes”

40f
The author’s statement is not the same as said in the reference (Denœud & Vergnaud, 2004) which reads “The frequent observation that tandem repeat-containing genes are often associated with outer membrane proteins suggests that such genes help bacteria adapt to their environment, …” . I just want to point out that TR regions do not encode proteins.

51f
Please rephrase the sentence. ”Sequencing … result in short DNA fragments” makes no sense. Sequencing results in reads.

59ff
The overview of de novo repeat identification methods should be extended. It is not sufficient to only cite the 15 year old VMatch. There are many other strategies out there.

63ff
This final paragraph is not completely clear to me and should be rephrased. Please also add at the respective sentence that NGS data was used.

Figure 1
The caption talks about 6 steps and nothing else. Please extend/adapt. It would be good to adapt the right hand side explanations to the style of the left box. A general aesthetic refinement of this figure is highly recommended.
If DACCOR is that modular as said in lines 86-89, it would be good to indicate this somewhere near the “identify repeats de novo”-box.

2) Methods

78f
The explanation of Step 3 is not clear to me.

80
Would it be possible to explain this mismatch identification in a kind of sketch? Especially the mismatch-marker addition sounds unique to me and is maybe worth a figure.

90/95
“repeat/repetitive region”: Please select one term and use it throughout the entire manuscript uniformly. I prefer “repetitive”.

100
“sequenced fastq files” sounds odd. Fastq files are generated during sequencing.

104
Why is BEST capitalized?

109-111
The name of this module could be given much earlier. Consider moving this tiny paragraph after line 85.
(minor remark: the name of this module is called “analyze” in the corresponding github README.md file)

114ff
This is too much of the term “reconstruction” and confuses the reader a lot. Please define other terms or at least rephrase this paragraph. For example, does “reconstructed subsequences” mean “reconstructed repeats”? What is the difference between “reconstructed regions” and “whole genome”?

119-123
This paragraph is pretty clear. It is also worth to consider putting the module names into the respective boxes of Figure 1.

128
Please avoid “several”, just give the number.  This is also a good place where the species are named once with their full name. Then please stick to the scheme to give at first appearance the full name and afterwards always in the style “E. coli”. Please avoid strain names (Nichols) if possible. Also the references to the bacterial genomes are missing (at least provide an accession number).

132
provide the number of samples (106?)

3) Results

144-148
This is contrary to line 130 where it is stated to use a max of 5. A max of 5 is not used for the VMatch comparison but only for the DACCOR-only repeat identification resulting in Table 2, right?

Table 2
replace “.” by “,” in 3.141. Please avoid “several”. There are also different spellings of “base pairs” throughout the manuscript (with and without dash).

162
The wrong supplemental figure is referenced (also in line 209)

Table 3
remove italics in caption

174f
This last statement is not clear to me. What is “almost all” and where does the “100%” come from?

181
Please provide the exact material reference (like “Supplemental Table 1&2”). I guess it is referring to the two csv files. They are actually not comma-separated but tab-separated. In addition, the 16S.csv lacks headers in the last columns. Although this header is provided in the 23S.csv, it is still not very descriptive and needs to be improved.

Figure 3
The labels (a)&(b) need to be resized

4) Discussion

213f
I assume this refers to Supplemental Figure 1, which is not referenced throughout the entire manuscript. Please refer to this comparison between DACCOR and VMatch in the results and discussion sections appropriately.

238f
Why twice max read length? It seems too long to me as reads can then be mapped without “touching” the repetitive region. If this is intended, then please explain it in the manuscript.

Generally, I support this article and encourage the authors to submit a revised version to allow a re-evaluation as I belife this automated pipeline for repeat reconstruction can be of interest to several fields of genomics.


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: DACCOR–DETECTION, CHARACTERIZATION, AND RECONSTRUCTION OF REPETITIVE REGIONS IN BACTERIAL GENOMES
Review round: 1
Reviewer: 3

Output:
Basic reporting: The authors propose an approach for reconstructing repetitive regions in bacterial genomes. There are several major issues and minor issues:

Major issues:
1. The authors claim their method DACCOR a novel method for reconstructing the repetitive regions. The first step (identify repeats de novo step) seems the only novelty step, as other steps more like pipeline that heavily relies on EAGER. However, the authors only use one paragraph (line 74-85) to describe this novolty part. Most of the descriptions are unclear, for example:
	1) In the "Merge k-mers" step, how the authors deal with circle or bubbles, and process branches?
	2) How the "Add mismatch marker" step goes? How can this allow lots of mismatches like 15 in supplementary figure 1? How to deal with indels?
	3) What is the "Filtering" step? No any description here.
Besides, for doing comparison, many other tools can also do the similar work efficiently and accuratly, for example RepeatScout, the authors need to prove why their approach DACCOR is better?

2. The authors compare the performance of the first step (identify repeats de novo step) against VMATCH in table 1, and use the VMATCH results as benchmark. Then, how can the authors prove their approach is better? If not as good as VMATCH, then why users prefer the authors' approach? In supplementary figure 1, the authors showed that their approach DACCOR is faster than VMATCH, especially when number of mismatches is large, but how accuracy of their approach? The results and comparison are not promising.

3. There are lots of available long reads can be used as benchmark data for comparison. The authors should provides comparison with promising benchmark data.

Minor issues:
1. line 298-332: the authors use half page to list the authors of a paper in reference! But only one paragraph for describing their major part of Method!!
2. The language shoule be improved, for example:
	1) line 75: the ... is divided into ... that occur more than once are stored.
	2) line 78: long regions consisting only of one base?
	3) line 139: 25 -> 25%
Experimental design: no comment
Validity of the findings: no comment
Additional comments: no comment


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

Input:
Title: DACCOR–DETECTION, CHARACTERIZATION, AND RECONSTRUCTION OF REPETITIVE REGIONS IN BACTERIAL GENOMES
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment here. Please see line-by-line remarks in the section “Comments for the author”.
Experimental design: No comment here. Please see line-by-line remarks in the section “Comments for the author”.
Validity of the findings: No comment here. Please see line-by-line remarks in the section “Comments for the author”.
Additional comments: The Authors addressed all my comments very well by either changing the manuscript or via a comment. This improved the manuscript remarkably but a few minor issues and a more serious one remain to be solved.

Minor:
L13: The part “of the genotypers” can be removed.
L24: Naming SPAdes this way in the introduction is not needed.
L73: Both de novo tools have the same reference.
L111: Would it make sense to add “separately” in this sentence to underpin the usefulness of DACCOR? “… and can be used SEPARATELY for the de novo …”
L116f: For me the sentence “Additionally…” looks redundant. If this is not a “special feature” (which  I then do not understand) it can be deleted.
L133-135: This paragraph feels redundant or at the wrong place. I think it can be deleted.
L143-147: This also repeats basically the lines written above. If the authors want to make the point, that “pipeline” connects the three modules, they should write this in a shorter/better way.
L148-151: Wouldn’t it make sense to put this paragraph right to the other one above that talks about “identify”?
Figure 1: The figure improved a lot. My only suggestion refers to the style of the detail boxes. I would prefer that they have the same grey background like the center boxes and have the included sub-boxed with a white background. This would emphasize that they are a detailed explanation of the three center boxes. This effect can even made be stronger by replacing the curly brackets by dashed lines between the corresponding corners of the boxes (a bit like in [1]). The “incoming” and “outgoing” arrows in the detail boxes should also be avoided as they are redundant with the arrows in the center column.
[1] https://www.researchgate.net/figure/Diagrammatic-cross-section-of-human-skin-including-a-zoomed-in-view-of-the-epidermis_fig1_321341598
Table 1: This is a very good overview. Please substitute the word “read-seq data” by something like “DNA-seq data” or “NGS data”. Also the number of samples coming from the 3 studies should be indicated either in this table or near L158 in the text. Simply to explain how they sum up to 106.
L156: The reference for VMatch was already given in L69.
Table 3: “different repetitive regions” needs to be explained in the text or rephrased in the table. I don’t understand what it is supposed to mean. Is it something like a repeat family?
Table 4: It should be indicated that this data refers to T. pallidum. Just out of curiosity, are the two copies of the 16S and 23S exactly the same length, because only the two numbers 1495 & 2900 are given. By the way, the thousands separators are missing.
L206-209: It should be indicated that the two longest regions contain both copies of the respective genes (1 region = 1 operon).
L223-232&L302: I’m not a variation specialist, but was always told “be careful with the term SNP as it refers to populations”. I suggest to replace SNP by a term like “site-specific / variant position” like it is already used in Table 4 and the Methods.
L225: Am I getting it correctly that these 36 positions are referring to the two 16S copies together? This means in turn that besides the 30 site-specific variations 6 are in common on both copies? If yes, this should be formulated a bit clearer, if no, it needs even more clarification.
L230: Change 2003 to 2,003.
L242: Change 1000 to 1,000.
L250: Set de novo in italics.
L256: “use a k-mer size” sounds odd. Maybe “choose” or “optimise”?
L261: “On the other hand, the k-mer size should also not be longer than half the length of the input reads” It should be explained why this is suggested.
L271: A period is missing.
Table 5: Thousands separators in the last column are missing.
Table 6: The sings in column “%N” are not consistent. The table could also be improved by either replacing the “%N” column by “% resolved bases” or adding a new column with these numbers. This is only a suggestion.
Figure 4: The caption should be improved with some additional information like starting with “Repetitive regions de novo identified by DACCOR…”.

General remarks:
Some Program names were not yet converted to Courier like RepeatMasker, BWA or GATK.
I recommend to change all occurrences of “mapping approach” to “mapping-based approach” throughout the manuscript. (for example in L241, 249, 296)
Although I found several typos, the manuscript should be checked again very carefully. For the next review-round I am expecting a much higher quality in this regard.

Major:
My original comment:
Line 80
Would it be possible to explain this mismatch identification in a kind of sketch? Especially the mismatch-marker addition sounds unique to me and is maybe worth a figure.

The Authors’ reply:
We explained it in more detail. However, we feel that if we add a figure, the focus will shift too much to this repeat finding approach and away from the actual reconstruction of repetitive regions, which is our main focus. The repeat finding itself is an integral part of DACCOR as we would like to publish it, but as we explained, it is not the main contribution and can be substituted.

My reply:
Although this paragraph was extended a lot, I am still not totally sure about this mismatch-marking. I do not agree with the authors’ reply. If the method is novel and part of that publication, it has to be explained in an adequate and understandable way. It is a methods focused paper. However, I understand that a figure in the main text really might shift the impression of the reader. Therefore, my suggestion is to make a supplemental figure.


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

Input:
Title: DACCOR–DETECTION, CHARACTERIZATION, AND RECONSTRUCTION OF REPETITIVE REGIONS IN BACTERIAL GENOMES
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: The authors have resolved many issues for my previous review, and the draft has been improved a lot. However, there are still one major and one small issues:
1) Major:
The major contribution for the paper is they propose a pipeline that can reconstruct the genomes, and also the repeats for individuals. However, it is hard to evaluate the accuracy of the constructed repeats and genomes. The authors have tried several indirect ways to "prove" their pipeline is accuracy, at least not worse than other tools. For example, they did statistic comparison at line 219-235, and also compared with de novo assembly results. The authors argue that long reads is not as common as NGS data, which is true. But they ignore that long reads can be used as a good resource for benchmarking their approach. And there are far more data can be used. For example, data released here: http://www.cbcb.umd.edu/software/pbcr/closure/index.html (there are even error corrected long reads can be used). So, it will be much more convincing if the authors can use long reads (and the assembly) as benchmark to evaluate their pipeline performance.

2) Minor:
I think this is the right way (authors should adjust according to PeerJ requirement) to cite this paper, not take half a page to list all the names:

International Human Genome Sequencing Consortium. "Initial sequencing and analysis of the human genome." Nature 409.6822 (2001): 860.
Additional comments: no comment


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

Input:
Title: DACCOR–DETECTION, CHARACTERIZATION, AND RECONSTRUCTION OF REPETITIVE REGIONS IN BACTERIAL GENOMES
Review round: 3
Reviewer: 1

Output:
Basic reporting: Please see "General comments for the author"
Experimental design: Please see "General comments for the author"
Validity of the findings: Please see "General comments for the author"
Additional comments: The Authors addressed my comments very well. I especially like the improvements in Figure 1 and appreciate the creation of Supplemental Figure 1.

Only 2 minor issues remain.

1) The SNV vs. SNP: I think my intention was mis-understood. I wanted to say, that the term SNV should be used instead of SNP because no “population-wide” frequency can be determined. SNP is often defined as a polymorphic locus with multiple alleles having a certain frequency (often >1%) in a population.

2) Supplemental Figure 1: This figure helps a lot with understanding the mis-match handling. I only stumbled over the equation in Step 5. It is not for all numbers intuitively clear to what they refer to (for example “-2” and “-12”).


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: DACCOR–DETECTION, CHARACTERIZATION, AND RECONSTRUCTION OF REPETITIVE REGIONS IN BACTERIAL GENOMES
Review round: 3
Reviewer: 2

Output:
Basic reporting: The authors have revised the required revisions.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The authors have revised the required revisions. And hope they can do the validation part with long reads in their future work.


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

Input:
Title: NON-BIOLOGICAL SYNTHETIC SPIKE-IN CONTROLS AND THE AMPTK SOFTWARE PIPELINE IMPROVE MYCOBIOME DATA
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The authors propose a standard method for internal control of metabarcoding data and related bioinformatics workflow. The techniques seem to be well refined and useable; minor comments are given below.

96	what do you mean by ’spike-in’? I have seen that ‘spiking’ is ascribed to the procedure, where a known-quantity control DNA/organism is co-extracted and co-amplified with a sample to provide information about the sample DNA quantity / extraction efficiency. Give a clear definition. Would your amplicons also work when adding a known quantity to a sample to be subjected to DNA extraction?
99	mock communities alone so not provide information about extraction success from soil or wood.
113	‘index bleed’ seems to have the most ambiguous meaning of the synonymous terms. Why prefer this one?
134	‘range of fungi, including paralogs,’ What is a paralogous fungus? Do you also mean species =fungi here?
280	what about ITS3 priming site? As ITS2 site?
374	I think that most authors consider also presence/absence but report quantitative analyses. Binary HTS data are more noisy because of tag switching and yields lower R2-values because of loss of quantitative information.
382	while this is true for absolute terms, you cannot claim this for relative term. It should be tested by varying the relative abundance of ingredient taxa and running regressions.
384	it would be really interesting to test this by running the entire mock using a metagenomics approach with no PCR.
407	see also a review of Balint et al. (2016) how information about sequencing depth can be included. Discussion of rarefying may be here beyond the scope.
472	give a formula, how this is calculated for each OTU. The main problem is with OTUs that dominate in some samples but are rare in others.
509	here you are mixing relative and absolute abundance.
516	highly concentrated DNA produce chimeras – a lot!
522	For IT, it is actually quality in the sequence end that becomes critical.
* The AMPtk platform is missing completely from the Discussion. At minimum, you should compare its features with other platforms that offer several analysis options, e.g. QIIME, PipeCraft, etc.

Leho Tedersoo,
Non-anonymous referee


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: NON-BIOLOGICAL SYNTHETIC SPIKE-IN CONTROLS AND THE AMPTK SOFTWARE PIPELINE IMPROVE MYCOBIOME DATA
Review round: 1
Reviewer: 2

Output:
Basic reporting: see comments below - this section "passes".
Experimental design: see comments below - this section "passes".
Validity of the findings: see comments below - this section "passes".
Additional comments: This study focuses on how mock communities can be used to validate and improve the results from high throughput amplicon sequencing (HTAS) of fungi. This tool is very widely used in microbial community profiling currently and efforts to check the biological accuracy of the results are continually needed.  The authors combine data based on two types of mock communities to show that there are important shortcomings with current HTAS analysis pipelines and then present a new pipeline (amptk) that overcomes many of those issues. While I would usually worry that blending the introduction of a new analysis pipeline with results from multiple mock validations would result in a very challenging paper to read, the authors do an excellent job of integrating the two in a way that is synergistic. Overall, the basic reporting is well articulated and the experimental tests are both comprehensive and easy to understand. Given the range of tests presented, the findings appear to be valid and well justified. I think this paper and pipeline represent an excellent addition to the field of HTAS-based studies of fungi and look forward to applying the Symmock and amptk pipeline in my own studies. Below are a range of relatively minor comments that I hope will help the authors improve the final presentation of their work.

L183- What is the justification for the higher then lower annealing steps in the PCR reaction – trying to reduce non-template amplification?

There are many parts of the results section that are redundant with the methods section. For example on L 305-307 there is a re-explanation of the cultures chosen for the Biomock.  Some additional detail is included, but I think that that info should have been presented earlier and then this paragraph could be eliminated from the results, since it is about “creating” the mock rather than explaining the results from that mock (which is what should be in the results section).  This may be a stylistic choice by the authors, but I think that making the methods a bit longer and the results more focused on the results will allow the reader to more clearly follow the manuscript.

L371-373 – Ihrmark et al. 2012 Figure 4 also shows a strong relationship between relative abundance of amplicons and relative abundance of template.

L461-462 – This is a really important additional test and I am excited to see the authors test the effect of sample OTU richness on recovery of the SynMock.  It looks like despite its simplicity in OTU richness, the SynMock is capturable in more rich samples and therefore likely a good representative mock to use.

L508-513 – Switching from relative abundance to incidence based analyses may have some major downstream consequences for ecological interpretation, so I suggest the authors consider also acknowledging that data transformations of abundance based data may help account for the skew present in HTAS datasets without the massive up-weighting of rare taxa that happens with presence-absence transformations.

L518-520 – This is similar to above comment about the structure of the manuscript.  Here the authors say that they tested the effect of cycle number (which they do), but I could not find the formal presentation of that test in the results section.  It would make more sense to me to have a clear set of sentences describing the result in the results section than having the reader go look in the supplemental figures to see the results.

L553 – I don’t disagree with this conclusion, but I am afraid the “horse is already out of the barn” on the use of abundance-based data in HTAS datasets for fungi.  The Taylor et al. (2016) paper makes a strong conclusion that read abundance is valid to use as a proxy, although their biomock is small (but phylogenetically broad).  One possibility is for the authors to run their own biomock with the Taylor et al. primers and see if they get better results than the ITS2 primer pair they used.  I’ll be surprised if they do and actually strongly agree with the authors that initial PCR-stage stochasticity is likely a major driver of variation in sequence reads in HTAS datasets (based on similar analyses in my lab).  Unfortunately, that is not an easily fixable problem as natural samples have many taxa that can’t be amplified individually and then pooled after PCR.  That said, Egan et al. (in press at Fungal Ecology) clearly shows that the repeatability of HTAS read abundances of replicates for a given sample is very high on Illumina. I think that some discussion by the authors reconciling the high precision across replicates with the high stochasticity of initial PCR would be helpful in advising readers on how to proceed with interpreting HTAS-based data.

Non-anonymous review by Peter Kennedy


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: NON-BIOLOGICAL SYNTHETIC SPIKE-IN CONTROLS AND THE AMPTK SOFTWARE PIPELINE IMPROVE MYCOBIOME DATA
Review round: 1
Reviewer: 3

Output:
Basic reporting: Paper reads well. Need to cite more literature. Please see below.
Experimental design: Experimental design is appropriate, however, the authors need to make sure that their designs are not out of date. Please see below for more details.

Parameters for processing data is requested.
Validity of the findings: Discussion should incorporate a few more current literature.
Additional comments: In "Non-biological synthetic spike-in controls and the AMPtk software pipeline improve mycobiome data" the authors created biological and synthetic mock communties to test the quality of sequence data processing through a pipeline that they have developed. The authors took some of the most important needs in the amplicon processing and solved them through this pipeline. This is important to the overall scientific community. However, because the field moved so quickly, some of those needs might have already been addressed by other researchers. Overall, the paper flows well, the data presented is straight-forward, and some components of the paper are crucial to the current use of high throughput amplicon sequencing.

I feel that the most important contributions of this paper is the development of the synthetic mock community, as well as the ability to use them to solve the issue of index hoping. These two components should be highlighted in the paper because it seems that more people are moving to the dual indexing system. This would be a major contribution to the scientific community.

Nature of the "story telling" narrative is appreciated and makes reading smooth and easy, however, parts of the "results" section really should be in the methods.

The problem with length in ITS might have already been solved by Robert Edgar. Please check with him and his website to see if this is the case. If the problem had been solved, then the manuscript needs to be updated to reflect that.

Please provide parameter files for the UPARSE pipeline when used.

The results here showing that equimolar mock communities do not so equal number of sequences as an output has been found in many other papers. I would suggest that the authors cite some of them.

The discussion of whether relative abundance or presence/absence should is still in debate among the community, but the authors should at least acknowledge that over a dozen papers have attempted to correct for relative abundance. I would highly suggest that they be cited and discussed.


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

Input:
Title: CHANGE OF NICHE IN GUANACO (LAMA GUANICOE): THE EFFECTS OF CLIMATE CHANGE ON HABITAT SUITABILITY AND LINEAGE CONSERVATISM IN CHILE
Review round: 1
Reviewer: 1

Output:
Basic reporting: Overall, the manuscript is well-written, the use of professional English throughout is clear and unambiguous (although some minor edits are indicated below), and conforms to professional standards of expression. The introduction provides sufficient background to the study. The literature references are up to date and sufficient.
The structure of the article conforms to the acceptable format. The figures are relevant to the content of the article (see below for suggestions regarding the manuscript's figures). The raw data has been made available, however, there seems to be a problem with the coordinates of the data provided (they are displaced to the east when mapped in a GIS, using the UTM 19S coordinate system).

Content edits
lines 129-131. The statement in the sentence starting with "For instance,..." does not seem correct. A generalist species tends to be more adaptable in the face of climate change. It is usually species with narrow or more specific habitat requirements and/or with low tolerance to environmental conditions that are more sensitive to climate change.

lines 394-395. In the sentence that starts with "Our worst-case scenario..." the authors should clarify that the percentage lost is for the Chilean range only.

Caption for Figure 1. I do not think it is necessary to explain all four software programs used in the analyses, as it was already explained in the main text.

Figures 2-4. It appears that the country labels in the maps could fit horizontally, which is visually better. The label for the Falkland Islands does not seem to be necessary, but if the authors decide to include it, it should be in a smaller font than the country labels. Also, in most maps it is shown as Falkland (Malvinas) Islands, as it is a disputed territory.

Minor edits
line 78. Replace "South American cone" with "southern cone"
lines 88-89. The sentence beginning with "In spite of this,..." does not actually contrast the statement in the previous sentence.
line 95. "West" should be in lower case
line 100. "Northwestern" and "Southwestern" should be in lower case
lines 116-117. should say "growth of vegetation"
line 121. Replace "discusses" by "discussed"
line 122. "..., as has been discussed elsewhere for other species." Should include citations.
lines 125-129. The sentence beginning with "However,..." does not actually contrast the statement in the previous sentence.
line 166: Should read "Species" instead of "Specie"
lines 178-179. "In time of future anthropogenic landscape transformations (citations)" is not a complete sentence.
line 182. All descriptions are in past tense, so change "We use..." for "We used..."
line 327. Replace "show" by "has"
line 363. Replace "worse" by "worst"
line 460. Delete "a" in "a 11% of the future guanaco distribution"
Captions for Tables 2 and 3. Replace "de" by "the" and "sever" by "severe"
Caption for Table 3. No need to explain the analysis here, as it was already explained in the main text. The caption can start with "The results in the table correspond...". Delete last sentence. Instead, consider using "If the empirical value is within the range of values observed in the percentages, the hypothesis of niche equivalence is supported (shown in bold type)."
Caption for Table 4. Delete last sentence. Instead, consider using "If the empirical value is within the range of values observed in the percentages, the hypothesis of niche similarity is supported (shown in bold type)."
Experimental design: The manuscript is within the scope of the journal and the research questions are well-defined. The methods are described in sufficient detail to be replicated by other researchers. However, my main concern with the study is the regional scope of the analysis (at the country level). The guanaco's distribution includes the southern half and north west of Argentina, south of Bolivia, and southwestern Peru. Therefore, restricting the analysis to Chile may have implications for capturing the full environmental range for the species. There are several studies addressing this issue (e.g. Pearson and Dawson 2003 GEB 12:361-372; Thuiller et al. 2004 Ecography 27:165-172; Barbet-Massin et al. 2010 Ecography 33:878-886; Titeux et al. 2017 DOI: 10.1111/ddi.12634). From Thuieller et al's (2004) main conclusions: "Using restricted data (similar to not capture the full species’ environmental range) reduces strongly the combinations of environmental conditions under which the models are calibrated, and reduces the applicability of the model for predictive purposes (Pearson and Dawson 2003). This problem has important implications when future projections of species distributions are sought. In particular, species niche from restricted data sets might be seen as analogous to the modelling of species niche from a limited geographic location not covering the complete range of environmental conditions in which species may occur." It would be interesting to see how the projected distribution of the guanaco in Chile may change if the entire environmental range is considered.
Related to the point above, looking at Figure 3, the larger areal gains in the different climate change scenarios are in southern Argentina, where the species already occurs.

Minor comment.
How were the CMIP5 variables processed to match the WorldClim variables?
Validity of the findings: As mentioned in the previous section, my main concern with the study is the generation of models with geographically restricted data. Using these models to predict distribution shifts under climate change may produce biased projections. Therefore, the validity of the findings may be questionable.
Additional comments: I suggest the authors redo the analysis including the entire range of the species.


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: CHANGE OF NICHE IN GUANACO (LAMA GUANICOE): THE EFFECTS OF CLIMATE CHANGE ON HABITAT SUITABILITY AND LINEAGE CONSERVATISM IN CHILE
Review round: 1
Reviewer: 2

Output:
Basic reporting: This is a potentially interesting work on current and forecasted distributions of guanaco Lama guanicoe in Chile, which could merits publication, but only after substantial changes and clarifications. The mss models both present day and forecasted distribution under different climate change scenarios, and a somewhat confusing section about niche divergence between species’ lineages. Besides, it includes some information about changes in protected distribution under the mentioned CC scenarios. The mss has some interesting results, although the mixture of hypothesis and analytical approaches makes its understanding somewhat difficult. I congratulate the authors for their extensive data set and the effort made in using modern techniques to analyse it.

The manuscript needs a deep English revision. Writing is in general rather wordy, and the text is oversized and confusing in some parts. The paper therefore would benefit from shortening and improving writing quality. Another problem is that, in general, writing tends to suggest that causality is demonstrated, but the authors should be careful about that, because the data presented here are correlational and results are strongly dependent on original variables used for the modelling. Another main problem of the paper is that statistical and modelling procedures are unclear.

Introduction
Introduction is rather long and worthy, as other sections of the mss, and should be substantially reduced. The main idea of the paper is rather hidden and I had difficulties to focus the paper. Some shifts of scale and conceptual jumps are found within and between paragraphs respectively. Objectives are not well connected with predictions. Especially, I found some inconsistencies in the relevance afterwards gave to some hypotheses (PNC and PND) and the little interest and justification given to them in the Introduction. Some recent references are needed, especially in the context of guanaco’ niche (see below).
I am especially concerned with the lack of clear predictions for these supposed phylogenetic relationships between lineages (see below).

References
Some basic and recent references are lacking. I suggest making some search, as I have done by myself, on guanaco and niche. See for instance: Traba et al., 2017. Oikos 126, Iranzo et al. 2013, Plos One.

Structure
Significant improvements have to be applied to fit the standards of PeerJ, both in relation to citing references and in figures and tables.

Figures
The mss has an inflation of figures. I suggest decreasing the number of figures. I have had some difficult in understand several of them, especially maps when colour print is lacking. Besides, several figures have typographic mistakes (see below). I suggest a thorough revision to easily amend these problems.

Raw data are supplied. However, some inconsistencies between maps and main text can be found, as the text is circumscribed to Chile, but maps show areas in Argentina and other countries. Please, authors should clarify this, as a main problem with original raw data may cause bias in modelling outputs (see below).
Experimental design: The paper is novel to my knowledge, and its findings could improve basic and theoretical information on guanaco, though it could be of special interest only for specialist.

Workflow is rather difficult to follow, and has some typographic mistakes. After reading the main text, I find this figure unnecessary.

One of my main concerns is related to raw data used for modelling present day distribution. As only Chilean distribution is analysed, only data from Chile should be used (but see my comment about Figures and maps). However, modelling only-climate distribution of a widely distributed ungulate with just a data subset may provoke a biased result about the climatic niche of the species. This is paradigmatic when analysing results from MaxEnt modelling, and this was made with just a small bunch of climatic variables, being all of them pretty relevant to explain the distribution of the three response variables: the two lineages and the species as a whole.

This is especially important when analysing phylogenetic relationships between lineages (which are not yet even subspecies, to my knowledge) of a potentially highly mobile species, and with a wide South American distribution. If these predicted phylogenetic differences (though lacking a direction of change) come from an evolutionary perspective, and the authors are not exclusively seeing the ecological output of a partial response to just a few predictive factors, they could not expect such changes on ecological time. As the distribution model is restricted to just the very same conditions of the present occurrences, and the authors do not consider all the many other locations of guanaco throughout the continent, they may perfectly be observing the result of local contingent plasticity, forced by historical processes. Including the whole distribution in the modelling could have driven to higher variability in input variables. I suggest to avoid this PNC/PND section in the mss, which could be exclusively focused on modelling present and forecasted distribution.

Regarding statistics, I have some concerns in relation to the myriad of stats used. I hardly follow all the methods, as clear research questions linked to methods are not so evident. Obviously, MaxEnt results are highly dependant on input variables, as AUC increases as correlation between variables does. As I have already mentioned my concerns on raw data, I have also some doubts about variables used in the modelling. As the authors have used only-climate variables, just on a subset of the spatial distribution, inconclusive and biased results may emerge. For instance, high similarity between lineages in relevance of climate variables is found. I suggest to include land-use / land-cover variables to improve the models and correctly asses the niche volume of the species (and its lineages). I also suggest to use other alternative methods to test niche overlap and segregation. I have some doubts about other packages, as Biosarn, which is not adequately explained. I have some doubts about two-tailed test (L304; see specific comments).
Validity of the findings: Discussion is in general rather speculative, and writing tends to give the impression that causality is demonstrated. Conclusions are vague and undefined, and deserve to be deleted.
Additional comments: Specific comments

Abstract

In general, I find the abstract confusing, though this could due to the necessity of improving the English. First sentence (L22-24) is unnecessary.
L26-28. Related to climate Change? Two very different objectives in the same mss.
L29 and ss. No information on data and methods is provided in the abstract. But information on the species is, what is already mentioned in the introduction.
L33-34. Contact population is inconcrete for the abstract.
L34. Prescribe?
L34-41. Authors should make an effort in shortening and clarifying these results.
L41. Lineages names should go above (L-27).
L43. Not necessary for an abstract.
L50. What is contact population niche?
L51-52. Final sentence is inconcrete and deserves deleting.

Introduction

L54-56. Unnecessary.
L56-61. Authors could consider merging but reducing here.
L61-68. Writing is wordy and confusing, mixing conceptual scales.
L75. Is Magellan the same than Magallanes (L73)? Please, clarify
L80. Roaming? May the authors want to say remaining?
L82-83. All the species are characterized by this.
L86. Is really necessary this?
L87. In spite of this? Maybe the authors wanted to say however?
L89. These qualities?
L91. Please, change feeds scavengers by is the prey of…
L94. Authors should homogenise the use of capitol or lowercase letters throughout the text. Please, see the standards of PeerJ.
L97. References are lacking here.
L105 and ss. All this about contact population is unclear. Does it  have individuals from both lineages? How do you know that? The distribution was predicted to occur? But is it or not? How is the relation with predictors?
L115. Please, see standards of PeerJ for citing references.
L116. Growth of
L122. References are lacking here.
L122 and ss. Overwriting, please simplify.
L125. However?
L126. Impressive? I don’t understand what the authors want to say here.
L127-132. It needs deep revision. Confusing and oversized.
L133-137. Already mentioned.
L137 and ss. Already mentioned.
L140. Is difficult to ascertain if this contact population does exist or is only predicted.
L141. This asseveration is not substantiated.
L144. I hardly share this asseveration.
L145 and ss. This argumentation is out of focus of the mss. Maybe it deserves another mss at all.
L153. Is ESUs the same than lineages?
L157. surface area seems to me somehow redundant.
L159. Change distributional by distribution.
L161. Niche equivalence and similarity are critical concepts, but unexplained in the mss.

Methods
Workflow seems to me unnecessary.
L168. Are these 364 additional records included in Gonzales et al 2013?
L169. Please, see standards of PeerJ for citing references.
L170. Are the authors mixing data from direct sights and indirect evidence? What effect may this have on results reliability? How do the authors assign sightings or, even worst, indirect evidences to one specific lineage? This is especially worrying in the contact zone.
L177. Please, delete possible.
L178-179. Meaningless sentence.
L180. Authors may model only-climate niche, but not for dismissing other variables.
L182. used.
L182. Authors should mention climate variables originally used.
L187-188. This is confusing. Dis the authors use PC components as predictor variables in the model? If authors used original variables, how it looks, and considering that PCA builds orthogonal components, it is unnecessary to test this, and of course the figure.
L193-214. All these paragraphs are confusing, and needs deep revision and shortening.
L196. What is GHG?
L206. No information about selection criteria is provided. Authors should consider the possibility of using just two GCM, the best and the worst case ones.
L213. Authors should consider the possibility of using just one temporal scenario.
L216. Please, change are by were.
L217. I missed something, or this is the first time of considering the Chilean distribution as a whole, and the two lineages separately.
L237. Please, change use by used.
L241. Guanaco distribution models
L241. Please, consider time frame or time band, instead of time slice.
L240-241. This math is unnecessary.
L242. Averaged.
L250. Description of averaging models is inconcrete. Why do the authors use two different averaging methods? This subsection also needs clarification.
L254. Areal gains?
L257. I missed Supplemental legends. Maybe is my problem, but please revise it.
L257. Does this figure refer to surface gains as negative values?
L264. AUC <0.9 are not really good models. Please, consider that including correlated variables tends to inflate AUC values.
L277. BioSARN needs more explanation.
L285. Why do you include RAMSAR sites?
L287 and ss. I feel out of focus all the aspects related to PNC and PND. Indexes I and D are little explained. Geographic niche space is different that ecological niche space, as it depends on intensity of use.
L300. Background test needs clarification.
L302. Random points generation and what for are little explained.
L304. Why a two-tailed test? Two things may be more similar than random, but not less…
L304. Why a significance threshold of 0.1?
L305 and ss. These hypotheses are not well explained and substantiated.
L307. What are positive outcomes?
L308. Re-writing.
L308. Lack of significance does not mean hypothesis validation.

Results
L312. Original variables should be in Supplemental Material.
L315. Fig S2 and S3 are irrelevant. Besides, some correlations are >0.79, but both remain in the analysis. Why?
L317. was given.
L318. was dominated.
L318. And bio4?
L320. And bio 4, bio 7 and bio 15?
L322. Fig S4. All the variables seem to contribute similarly. How do the authors discriminate between variables? Something seems wrong when all the variables are similar in their contribution to the model.
L327 and ss. This seems somehow irrelevant to me, but it the authors do include it, it deserves an explanation.
L334. Fig 2. I can see other regions out of Chile modelled. How these locations have been selected? Why just a few ones? Guanaco was historically introduced at the Falkland Islands, why the authors do use these data, but not others in the continent?
Fig 2 shows no high quality area (just 23km2). Is not this rare, when some of the best guanaco areas in the continent are included in the modelling? This could be a mask effect of using only-climate data in the modelling.
L337. What Table?
L339-344. Comparisons between scenarios and time frames are confusing. Please, consider the possibility of using just one time frame.
L343. What are the original values? Citing Table 1?
L345-360. Results about surface changes under CC are somehow confusing. One could expect that, with an only-climate model, changes in surface after CC are going to happen. However, with this only-climate model one cannot ascertain if changes on guanaco distribution are going to happen as well, as guanaco may respond to other many factors than only climate.
L346-349. Percentages refer to threshold value, not to losses or gains, and therefore this is confusing.
L348. How do you consider significance, if it is just 23km2?
L353. I hardly see this.
L364. Please, delete Interestingly.
L372. See above comments on background test and two-tailed test.
L375. Please, see standards of PeerJ for citing references.
L379. Please, delete In spite if this.
L380. What are “important statistical differences”? This does not emerge from MaxEnt result.
L384. shows.
L387. Please delete “and”

Discussion
In general, it is rather long and little concrete.
L395. Delete comma after Although
L396 and ss. Authors should try to avoid referencing figures and tables in Discussion, except when it is essential.
L404. I feel that none of this is really extracted from your results.
L407. Please, delete For instance
L408 and ss. Is it ENSO? Is it so rare?
L413. Substantial reductions. I feel this does not emerge from your results.
L414 and ss. I do not understand how the authors relate these study cases with theirs.
L419. Maybe the authors prefer to start the sentence with In the case of…
L422-423. Pretty local references.
L424-426. Rewrite, please.
L427. See my main comments about phylogenetic-ecological relationships.
L426-427. I feel that this comes from a different methodological and analytical approach, very far from this mss.
L429. Idem.
L434 and ss. Confusing, needs rewriting.
L435. A non significant result does not allow to reject hypothesis.
L440. Please, see standards of PeerJ for scientific names.
L445. I think a significant is missing.
L447 its climatic.
L446 and ss. Again, I think that there is some confusion between evolutionary and ecological processes.
L454. Since?
L463. Maybe, the authors would consider to begin this sentence with Projected distribution models…
L467-470. This last sentence is irrelevant, and I do not share it.

Conclusions
I feel that this whole section is irrelevant for the mss, and may well be supressed.

Table 3 / Table 4
Results in the table…
Here authors mentioned a one-tailed test. Is it one or two-tailed?
I admit that Tables 3 and 4 seem to be crucial for the mss, but they are really difficult to understand.

Figure 1
Four software?
[…] in the generation of the models – What models?
The averaging procedure is little explained in the main text. Are there any references to support this? How the averaging is made? Weighted?

Figure 4
Numbers and letters in the legend do not correspond with those in the figure.


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

Input:
Title: CHANGE OF NICHE IN GUANACO (LAMA GUANICOE): THE EFFECTS OF CLIMATE CHANGE ON HABITAT SUITABILITY AND LINEAGE CONSERVATISM IN CHILE
Review round: 2
Reviewer: 1

Output:
Basic reporting: All my comments in this section have been satisfactorily addressed by the authors.
Experimental design: Most of my comments have been addressed. However, my main concern regarding this manuscript still remains, namely, the use of a geographically restricted data set to model the environmental niche of the species. The authors have included a couple of sentences in the discussion regarding this issue, but I am not completely convinced it is sufficient. The authors mention that "the net effect of our conservative predictions may underestimate current and future species distribution beyond its administrative boundaries", but I don't think this is the main problem (or at least, not the one that I was trying to point out in my first review). The problem is that not capturing the entire environmental range of the species may underestimate the current and future distribution of the species WITHIN the boundaries of Chile. For instance, the species may be using a range of environmental conditions outside Chile that are currently not represented by the presence localities in Chile. Thus, when projecting the future distribution within Chile, these areas will appear as not environmentally suited for the presence of the species. This may not be too problematic if you are assessing "the evolutionary aspect of niche conservatism hypotheses", but it may be if you are estimating the area (or percentage) of range contraction and the area (or percentage) of the range in protected areas.
Validity of the findings: Again, the validity of the findings depend on how much you trust that the presence data used in the study (restricted to Chile) represent the entire environmental niche of the species. I think this needs to be more thoroughly discussed.
Additional comments: Thank you for addressing my comments. I believe the manuscript has been greatly improved. However, I still believe that an effort should be made to include the entire distribution of the species in the analysis. Have you tried obtaining data from GBIF? I know these data may have problems, but with some careful screening, reliable data can be obtained from their database.


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: CHANGE OF NICHE IN GUANACO (LAMA GUANICOE): THE EFFECTS OF CLIMATE CHANGE ON HABITAT SUITABILITY AND LINEAGE CONSERVATISM IN CHILE
Review round: 3
Reviewer: 1

Output:
Basic reporting: All my comments have been addressed.
Experimental design: The caveats included in the discussion address the concerns that I have expressed.
Validity of the findings: The caveat included in the discussion regarding the validity of the findings addresses the point that I raised in my previous review.
Additional comments: I believe the manuscript has been greatly improved and I do not have any other major comments/suggestions.