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: ANURAN DIVERSITY INDICATES THAT CAATINGA RELICTUAL NEOTROPICAL FORESTS ARE MORE RELATED TO THE ATLANTIC FOREST THAN TO THE AMAZON
Review round: 1
Reviewer: 1

Output:
Basic reporting: The subject of the manuscript is interesting and important for the comprehension of the past connections between the Amazon and the Atlantic Forest through Northwestern Brazil. Nevertheless, I bring some considerations for manuscript improvement, considering that it can be a good contribution to the field.

The instrumental use of the English is good, but somehow it could be improved a little more, prioritizing fast reading. Actually, it is not an instrumental English issue, but a scientific writing issue, trying to present an overview of the subject, a gap of knowledge, and your contribution to the field in a more objective way.

Objectives are not well exposed in the introduction. The first five paragraphs position the reader to the climatic fluctuations of the Pleistocene and their effects on the Northwestern Brazil’s vegetation dynamics. They also show some studies supporting mesic vegetations inside the Caatinga (“brejos de altitude”) as a “footprint” of an ancient connection between the Amazon and the Atlantic Forest, as exposed in the text. Nevertheless, it does not bring the author to the objective of the work, which seems to test the hypothesis of “brejos de altitude” acting as this “footprint” of a past connection between the Amazon and the Atlantic Forest (or assessing how each biome – Amazon and Atlantic Forest – contributed to the formation of this connection, providing species that were sampled on the “brejos de altitude”, if these contributions were similar or not). Actually, I didn’t find a hypothesis in the introduction. In my opinion, these five paragraphs could also be reorganized in just three, with the same amount of information. Doing so, you must have more room to explore your objective, hypotheses, and approaches to assess your objectives.

Still about these first paragraphs, the literature used for background to the subject is classical (Haffer, 1969; Vanzolini & Williams, 1970; Vanzolini, 1981; Andrade-Lima, 1982; Oliveira-Filho & Haffer, 1995; Haffer & Prance, 2002; Costa, 2003; Auler, 2004; Santos et al. 2007) and used precisely. Nevertheless, there are more recent studies that contributed to the state of art of the field and should be included in. There are some in terms of phylogeography and ecological niche modelling:

PRATES, I.  et al. A mid-Pleistocene rainforest corridor enabled synchronous invasions of the Atlantic Forest by Amazonian anole lizards. Molecular Ecology, v. 25, n. 20, p. 5174-5186,  2016. ISSN 1365-294X. Disponível em: < http://dx.doi.org/10.1111/mec.13821 >.

SOBRAL-SOUZA, T.; LIMA-RIBEIRO, M. S.; SOLFERINI, V. N. Biogeography of Neotropical rainforests: past connections between Amazon and Atlantic Forest detected by ecological niche modeling. Evolutionary Ecology, v. 29, n. 5, p. 643-655, 2015/07/03 2015. ISSN 0269-7653. Disponível em: < http://dx.doi.org/10.1007/s10682-015-9780-9 >.

LEDO, R. M. D.; COLLI, G. R. The historical connections between the Amazon and the Atlantic Forest revisited. Journal of Biogeography, v. 44, n. 11, p. 2551-2563,  2017.  Disponível em: < https://onlinelibrary.wiley.com/doi/abs/10.1111/jbi.13049 >.

COSTA, G. C.  et al. Biome stability in South America over the last 30 kyr: Inferences from long‐term vegetation dynamics and habitat modelling. Global Ecology and Biogeography, v. 27, n. 3, p. 285-297,  2018.  Disponível em: < https://onlinelibrary.wiley.com/doi/abs/10.1111/geb.12694 >.

The Introduction’s last paragraph tries to justify the use of modern distribution of species to answer questions that deals with the past (ancient connections between the Amazon and Atlantic Forest) and also tries to justify the use of amphibians in this approach. In my opinion, more literature should be incorporated in this last paragraph, in order to give more support to the approach of using modern distribution of species to assess questions of the past. Apparently, you included more references to justify the use of amphibians for your objectives than to justify the approach of using current species distribution data to assess past phenomena. Therefore, more literature should be included in order to support your approach.

Still about the last paragraph. Please, expose the problematic to be assessed by your study. Please, try to answer these questions as well: why is your study a good contribution to the state of the field of ancient connections between the Amazon and the Atlantic Forest? In what level your study contributes to the knowledge about past connections between the Amazon and the Atlantic Forest through the “brejos de altitude”?

I have also noticed that you cited unpublished data and personal communications. I recommend you to cut them out of the manuscript, since these studies were not submitted to peer review for publication and we are not sure of the validity of these conclusions.

This paragraph is just a suggestion. The title is a little bit vague and not consonant to the conclusions of your work. I think they should be changed to something more direct, such as “Anuran diversity indicates that Caatinga relictual Neotropical forests are more related to the Atlantic Forest than to the Amazon”. Faster (19 words) and tell all the story. Please, take it just as a suggestion.

This paragraph is just a suggestion. Considering the purposes of this journal and some other authors proposing more reproducible studies, would you like to include the original species matrix you used in your analyses as a supplemental material? Please, take it just as a suggestion, considering reproducibility criteria.

Figure 1 to 4. Please include in the captions a mention to the supplementary material.
Experimental design: The study is an original primary research due to its approach, even not using primary data, but data from literature. Nevertheless, the research question is not well defined and should be included in. It also does not state how the research fills an identified knowledge gap. Nevertheless, the subject is relevant and meaningful.

I have noticed that you excluded some taxonomic inconsistencies prior to analysis. However, why do you use species with “cf” in the analysis? In my opinion, It seems as imprecise as categories such as aff, gr, and sp. I think you should show in the text a reason for that.

I have noticed that you included biotas from the Amazon, Atlantic Forest, Brejos de Altitude and Caatinga into your analyses. However, why did you not include Cerrado into your analyses? There are some “brejos” that contain a significant amount of Cerrado species on it (e.g. Crato), supporting the inclusion of some Cerrado localities in the analyses. Moreover, hypotheses of pluvial forests expansions and retractions through the Pleistocene are also coupled with expansions and retractions of other biomes nearby (Cerrado and Caatinga as well).

Moreover, why did you not try to use a stricter biogeographical analysis, such as Cladistic Analysis of Distribution and Endemism (CADE)? The use UPGMA is interesting, but it is not considered an “biogeographical” analysis per se. Please, provide in the test a reason you would rather UPGMA than a CADE. Notice that a study cited in your introduction (Costa et al 2007) uses PAE and CADE for the same purpose you did. In my opinion, you had better use a CADE with branch support (e.g. Bremer) instead of dendrograms, but if you have a good reason for using dendrograms, please provide in the text.
Validity of the findings: The results show some novelty not assessed before. The discussion presented is interesting. Maybe it could include some sentences or a paragraph more when including Cerrado biota into analysis.
Additional comments: The study is interesting and has potential for publication. Nevertheless, there are some issues that need to be tackled.


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: ANURAN DIVERSITY INDICATES THAT CAATINGA RELICTUAL NEOTROPICAL FORESTS ARE MORE RELATED TO THE ATLANTIC FOREST THAN TO THE AMAZON
Review round: 1
Reviewer: 2

Output:
Basic reporting: OK. The authors should avoid the use "personal communications" and unpublished data. They did not test hypothesis, they use cluster analysis.
Experimental design: The main concern about the study is that the methods the authors used do allow infer “process” on the relation of “Brejos” with Amazon, Atlantic Forest and Caatinga, but only “patterns”. The used cluster and ordination analyses, which could be nice to reveal patterns, but not to infer process. To do this, the need to use phylogenetic/phylogeographic information.
Validity of the findings: The findings were ok to reveal patterns, but they should avoid use them to infer process.
Additional comments: Dear author,

First, I would like to thank the opportunity to contribute with your manuscript. The manuscript untitled “What does the diversity of anurans have to say about relationships between a relictual Neotropical forest and the Amazon and Atlantic forests?” provide an interesting information about the relationships about these areas. However, there are several points that should be addressed prior the publication. I did several comments on the pdf file, which I think should be very important for the manuscript. The main concern about the study is that the methods the authors used do allow infer “process” on the relation of “Brejos” with Amazon, Atlantic Forest and Caatinga, but only “patterns”. Again, thanks for the opportunity, and I hope that my suggestions help the authors in their manuscript.


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

Input:
Title: ANURAN DIVERSITY INDICATES THAT CAATINGA RELICTUAL NEOTROPICAL FORESTS ARE MORE RELATED TO THE ATLANTIC FOREST THAN TO THE AMAZON
Review round: 2
Reviewer: 1

Output:
Basic reporting: Overall, the written text was well improved if compared to the first draft. It was improved in textual logic, what improved its structure and quality. The objective was also clearer compared to the first draft, which also improved the quality of the discussion section.

Fig. 1 has a green point out of map range.

The only criticism I still have to this study is applied to the statistical analysis. After analyzing the first draft, we suggested the use of a stricter biogeographical analysis (CADE) instead of clustering analyses, because clustering approaches cannot be used to infer biogeographical processes, but only patterns (even criticized, CADE creates groups based on shared presences and common ancestry, whereas ordination approaches create groups based only on overall similarity). In other words, even criticized among some biogeographers, CADE is a better alternative than clustering analyses. Moreover, the papers cited by the authors (Morrone 2014; Nihei 2006) do not prohibit the use of PAE/CADE methods, but recommend the use of it in specific cases (such as in exploratory contexts or in dynamic approaches). What should be avoided is the indiscriminate use of the analysis.

The authors also justify the use of clustering approaches based on a recent study (Barroso 2016), applied to prosobranch gastropods. Nevertheless, this study is clearly more applicable to a community structure level (beta diversity, and not to historical biogeography), inferring patterns of species distribution rather than processes. As this study is anchored in a historical issue (ancient connections between the Amazon and the Atlantic Forest through “brejos”), the use of clustering approaches will clearly impoverish your discussion and conclusions.

In short, a CADE is not the most appropriate approach for some biogeography studies (and it was used extensively used since in its inception. That is the real problem).  Nevertheless it is certainly a better alternative than a cluster analysis, because the former creates groups based on shared presences and common ancestry, whereas clustering approaches create groups based only on overall similarity, including noise to your analysis and not inferring process, just patterns. Therefore, the support for the use of a cluster analysis by the authors is weak. Obviously, CADE was just a suggestion. Other biogeographic methods could be used as well (i.e. Endemicity Analysis, considered to perform better than PAE; or even other methods). Another alternative is to make both analysis together (cluster and CADE) and compare the results.

Considering that the most important point of my suggestions was not properly considered, unfortunately I am not able to recommend the study for approval, although I noticed very significant improvements from the first version to this one.
Experimental design: already mentioned in "basic reporting".
Validity of the findings: no comment.
Additional comments: Considering that the most important point of my suggestions was not properly considered, unfortunately I am not able to recommend the study for approval, although I noticed very significant improvements from the first version to this one.


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

Input:
Title: DETECTION AND VARIABILITY ANALYSES OF CRISPR-LIKE LOCI IN THE H. PYLORI GENOME
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1. In general, the language used in the article is clear and proper. There are point sections that require attention, such as:
a.	Line 99: seems to be missing an article.
b.	Line 101: Correct National Biotechnology Information Center for National Center for Biotechnology Information (it is after all NCBI, not NBIC).
c.	Line 199: an unnecessary “of” at the end of the sentence.
d.	Line 253: Correct Csa3 for Cas3.
e.	Lines 163, 178: Correct VplC for VlpC.
f.	Lines 127, 146: Standardize the notation for VacA-Like gene. In line 127 appear non-capitalized.
g.	Lines 136, 187, 201, 222, 234, 244: In the first three, the local alignment nucleotide algorithm is presented as “blastn”. In the other three it is capitalized. The former is the customary (and original) version.
h.	Various lines: Italicize multiple occurrences of “Helicobacter” or “H. pylori” that appear in regular text (I stopped keeping tabs after the first few).

2.    The range of subjects presented by the cited references is adequate for the thematic content of the article.
a.	Standardize the formats in the list of references. Some journal names appear in italics, others in regular text. PLoS is presented in reference 29 as PloS.
b.	Reference 5 is missing the journal name and volume number.

3.	Professional article structure, figs, tables. Raw data shared.
a.	The range of figures is adequate for what the authors hope to illustrate. The images are of low-resolution, making it hard at times to discern the details (e.g., Fig3 or FigS1b).
b.	The legend to Figure 3 cites three groups, which one assumes are the three gray bubbles that group the branches of the phylogenetic tree presented, but the groups are not labelled to indicate their correspondence.
c.	Supplemental figures need legends. The details contained within each one of them are not sufficiently clear when cited in the main text, so more clarity is needed in a legend.
d.    All raw data is publically available. The authors thus fulfill this requirement.
4.	Self-contained with relevant results or hypotheses.
a.	The article represents a coherent and complete (within the scope of the design) unit of work. The design is consistent with the hypotheses presented, and the results speak to the questions posed.
Experimental design: 1.  The article presented constitutes original and primary research within the scope of the journal.
2.  The research question is well defined, originating from an identified gap in the knowledge of the organism in question, and anchored in the recent literature. The work identifies the CRISPR-like elements in the genomes of a broadly distributed sample of Helicobacter pylori strains, a species in which these elements had been reported as not functional and thus perhap non-present. With the identification of the vestigial elements, they expand provide additional information for the reconstruction of the role of the vestigial elements in the process of genome evolution. The authors place the findings in an evolutionary context, noting biogeographical associations and phylogenetic associations behind the patterns observed.

On line 114, regarding the construction of phylogenetic trees, one is to assume that all other parameters not explicitly mentioned were used with default values, right? Also, the evolutionary model is indicated, but not the type of tree that was constructed. Please provide more details to enable replication of your results.

On the re-construction of phylogenetic relationships among spacers (results reported starting on line 160), it is not clear how the "consensus" sequences for the spacers in group 4 were constructed. Which of the various spacers were used? Were all of the spacers in the non-VlpC locus considered, or also only the first three positions? Please clarify the approach for the reconstruction of that phylogeny.
Validity of the findings: The data are robust, originating from stardized public repositories. The derivations therefrom are in accordance with questions addressed, following standard methods and tools in bioinformatic sequence comparison and analysis. It is not clear, however, that the divergence patterns observed in the CRISPR-like elements represent a new tool for resolving standing biogeographical questions, or simply re-inforce the patterns previously observed, so caution must be exercised to not overinterpret the implications of the observations. As a closing statement the authos declase "this work highlights the importance of this type of sequences, which seem to have lost their initial function, in the variability and genomic evolution of H. pylori". Care must be used with the word "importance" as it relates to the roles suggested, for while the elements may be playing an incidental (though not necessarily inconsequential) role in the genomic evolution of H. pylori, and even if they have been suggested as direct participants in regulatory functions by other authors, their "importance" in the biology of the organism is not directly addressed by the observations presented.
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: DETECTION AND VARIABILITY ANALYSES OF CRISPR-LIKE LOCI IN THE H. PYLORI GENOME
Review round: 1
Reviewer: 2

Output:
Basic reporting: clear
Experimental design: clear
Validity of the findings: clear
Additional comments: Review of “Detection and variability analyses of CRISPR-like loci in the H. pylori genome”
Full paper summary:
This article uses Helicobacter pylori, one of the important human pathogens, to collect the entire genome of 53 strains of H. pylori from different regions. Although the functional CRISPR-Cas system has not been found in the genomes of these strains, CRISPR like loci have been recently identified. Based on this, the authors performed bioinformatics analysis on the CRISPR-like loci present in these strains. In this work, the authors analyzed 53 genomes from different geographic regions for searching and analyzing the variability of this CRISPR-like locus structure. This article confirms the existence of a CRISPR-like locus present in the VlpC gene in all genomes previously reported, and the authors also characterize new CRISPR-like loci in other genomic locations. In addition, the evolution and possible role of these loci were discussed by studying the variability and gene location of these CRISPR-like loci. Finally, the authors confirmed the feasibility of the CRISPR-like locus sequence as a phylogenetic marker for H. pylori and associated different strains with geographic regions.

Review opinion: (Final decision: substantial revision)

1.	There are only 53 species of Helicobacter pylori currently found. Why not choose all kinds of Helicobacter pylori for bioinformatics analysis to improve the persuasiveness of this conclusion?
2.	Authors must indicate when to collect relevant CRISPR information on the CRISPRs Database.
3.	The authors should describe in more detail the virulence, virulence, and effects on human health of Helicobacter pylori.
4.	In P114-115, the authors need to explain in more detail how to build a phylogenetic tree, such as distance-based methods using Minimum Evolution or Neighbor-Joining. In addition, using the nucleic acid sequence to construct a phylogenetic tree, the Kimura 2-parameter model is generally used. Why should the author choose the Jukes Cantor model?
5.	Please indicate whether there is a palindrome in the repeat sequence in the selected CRISPR locus？If it exists, it is necessary to discuss the RNA secondary structure that it can form.
6.	In P128, the author must point out the basis for choosing the reference sequence of strain J99?
7.	In P234-240, the author must clearly explain the 39 CRISPR1-like sequences mentioned in this, is this contrary to only the 22 CRISPR-like loci found in P144-145?
8.	The author must explain what principles are used to distinguish between CRISPR sites and CRISPR-like loci when analyzing the genomes of these strains.
9.	In P309-311, the authors are asked to elaborate on the potential of CRISPR-like loci to regulate gene expression.
10.	Please add a description about the diversity of CRISPR-like loci caused by genetic degradation, genetic recombination, gene insertion, etc., and its application in bacterial typing.
11.	Please increase the resolution of figure 3, Supplementary_Fig_S1_A, Supplementary_Fig_S1_B to enhance readability.
12.	The related publication on CRISPR Loci of foodborne pathogens below should be cited to discuss the research background and results.
Study the Features of 57 Confirmed CRISPR Loci in 38 Strains of Staphylococcus aureus. Front. Microbiol. 9:1591. doi: 10.3389/fmicb.2018.01591


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: LABEL-FREE QUANTITATIVE PROTEOMIC ANALYSIS REVEALS POTENTIAL BIOMARKERS FOR EARLY HEALING IN CUTANEOUS LEISHMANIASIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript (#31402) submitted to PeerJ, entitled “Label, free quantitative proteomic analysis reveals potential biomarkers for early healing in cutaneous
Leishmaniasis”, whose aim was to compare the proteomic profiles in patients with Cutaneous Leishmaniasis (CL) before and after 7 days of treatment and identify early biomarkers of curative response.  Twelve proteins showed differential expression in the comparative LC-electrospray ionization MS/MS (LC-ESI-MS/MS) by triplicate analysis. Seven of them were up-regulated and five of them were down-regulated. It was confirmed that three of the seven up-regulated proteins also had increased expression of their mRNA.

The purpose and approach are quite interesting in the area and the manuscript may attract the attention of several readers. However, several points must be clarified.

The authors state that “The aim of this study was to find and validate early biomarkers of therapeutic response in CL using proteomics without labeling in order to provide patients with adequate monitoring and identify early treatment failure, thus providing the possibility of changing the therapeutic scheme in a timely manner.” However, there are no validation tests of the biomarkers, only an mRNA quantification of 3 candidate proteins, whose increased expression was confirmed. Also, how could they identify early treatment failure if there are no patient samples with this characteristic?
Experimental design: Another very important point that needs to be better described is in relation to the sample. The number of patients and samples do not seem clear to me. It was also not possible to understand whether technical or only biological triplicates were made. In METHODS section, line 99: “ Four patients with a parasitological diagnosis of leishmaniasis with confirmation of  species by PCR-RFLP were recruited.” Shortly thereafter, line 189 “Six patients were included in the validation assay.” In RESULTS section, line 240: “three of the four biological replicas”, and still in line 288 “All 5 patients were cured after 6…”
The experimental design is not clearly described. It would be useful to include a schematic describing the experimental design, or to describe this more clearly the text. How many patients, how many samples of each patient were prepared and loaded on the gel? And on the LC-MS/MS, or on the mRNA?

It can be seen from the title as well as in the M & M that label-free proteomic approach was performed. However, the authors seem to make some mistake in the section results quoting label-based quantification (Line 240-241, line 267).
As is the standard in proteomics work, I suggest that identified proteins be categorized according to GO. The GO defines concepts/classes used to describe gene function, and relationships between these concepts. It classifies functions along three aspects: molecular function, cellular component and biological process.
Validity of the findings: In RESULTS section, What is the correct HDB (line 258) or HBD (line 283)?
About DISCUSSION section, it could be very interesting for the authors to define a touchstone for the proteins that will be considered in this section. As it is written, it was not possible to understand why some proteins are there, for example Keratin, type II cytoskeletal 73 and LAMP2, KRT10 and ATP7A.
In addition, it may be that the lines 326-332 are dispensable.

Figures 2A as well as 3B are dispensable.
Figure 4 - it might be interesting to note if the proteins are up or down regulated.
Caption Figure 5 is so confuse. Rewrite.
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: LABEL-FREE QUANTITATIVE PROTEOMIC ANALYSIS REVEALS POTENTIAL BIOMARKERS FOR EARLY HEALING IN CUTANEOUS LEISHMANIASIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript titled “Label-free quantitative proteomic analysis reveals potential biomarkers for early healing in cutaneous leishmaniasis” aims a critical issue regarding the disease combat. The manuscript is well written and minor correction in English are required. The data is showed correctly in the tables and figures. The authors applied cutting edge technology to search for biomarkers and reveal new proteins for future research.
Experimental design: The experimental design was well drawn; the distinct stages of the work were carefully and diligently put together. And overall the experimental design is ok! The material and methods section is well written and have sufficient details to be replicated if necessary.
Validity of the findings: In my consideration, there are some important questions not addressed by results and not discussed in the manuscript; The proteome of the leishmania parasite is been found to hold almost 50% of hypothetical/Uncharacterized proteins and it is surprisingly that in a wide proteome analysis, no one of these proteins was found. The authors cited an article (reference 5) in which hypothetical proteins were assayed. Another concern is about statistical validity of the results, the authors performed all the assays with a very low number of patients. These facts should be stated in a paragraph in the discussion section.
Additional comments: The manuscript entitled "“Label-free quantitative proteomic analysis reveals potential biomarkers for early healing in cutaneous leishmaniasis” represents a nice piece or work and a good contribution to the of new biomarkers. The manuscript is well written and organized.


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: LABEL-FREE QUANTITATIVE PROTEOMIC ANALYSIS REVEALS POTENTIAL BIOMARKERS FOR EARLY HEALING IN CUTANEOUS LEISHMANIASIS
Review round: 2
Reviewer: 1

Output:
Basic reporting: I believe that, following the revisions, in the current version the article is suitable for publication
Experimental design: I believe that, following the revisions, in the current version the article is suitable for publication
Validity of the findings: I believe that, following the revisions, in the current version the article is suitable for publication
Additional comments: I believe that, following the revisions, in the current version the article is suitable for publication


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

Input:
Title: ASSIGNING CONFIDENCE SCORES TO HOMOEOLOGS USING FUZZY LOGIC
Review round: 1
Reviewer: 1

Output:
Basic reporting: Overall the language is clear and well-written and wholly appropriate for a scientific publication.

The background is generally well described, although the use of confidence scores in other orthology/paralogy methods could have been discussed briefly (e.g. InParanoid, but possibly others) and what approaches they use. Similarly, the authors could discuss any relevant literature showing that synteny, genetic distance or gene copy number are useful variables for assessing whether genes are homoeologs.

The layout of the material is clear and the figures are similarly clear and well labelled. (Figure 4B, should include the units for distance, i.e. PAM units)

The manuscript is coherent and self-contained.
Experimental design: The paper defines the a meaningful question (how to assign confidence scores to putative homoeologs) and the study contributes an answer to this.

The work appears to have been carried out rigorously and the method are clear.
Validity of the findings: I have some doubts about the language used to describe the findings. These are relatively minor, affecting one statement in the abstract and a couple of expansions on this statement in the main text.  It doesn't have any impact on the validity of the paper but I'd suggest removing the claims, as detailed below:

The method is developed and the results (the confidence score) compared to an 'independent metric' (line 258), the total number of orthologs for the putative homoeolog pair. The authors reason:  "Homoeolog pairs with few orthologs are either lineage-specific or dubious, whereas pairs with many orthologs represent those likely to be true". However, they find the correlation between their confidence score and this measure to be R=0.006. In the abstract the authors say the metric corroborates their confidence scores. In my view, such a low correlation shows that either the confidence scores are a very poor measure or the independent metric is. I don't believe it corroborates them.

The authors also do a manual evaluation (Supplemental Table 1 and lines 264-270). I thought this was a lot better for assessing the described confidence score and was useful to the reader. The comparison with the old scores from 271-281 is also useful.

My suggestion is that the reason for the very poor correlation is that the independent metric is actually poor, not their confidence measure. I think the independent measure can be included in the paper but I don't think the claims made from it are valid. Figure 8 is used to suggest that despite the almost zero correlation that their is a general trend. There aren't any statistical tests to confirm this. By eye, the figure seems to suggest two classes, 'low' and 'high', like their old measure. As such, I think the authors should remove the claims based on this independent measure. I'd suggest - not saying in the abstract that the independent metric corroborates the confidence score - not calling it a 'benchmark' on line 77 (it isn't used as a benchmark) - not saying on line 317 "the resulting scores proved meaningful in how they correlate with the number of orthologs"
Additional comments: Overall I thought the paper was clearly written and addressed the research question posed. The methodolgy was sound. There are a couple of minor points that could be addressed:

Figure 5: The synteny membership function for 'high' decreases as the synteny scores increases above ~0.7 for all species. This means that a score of 1.0 belongs to the 'high synteny' class less strongly than a synteny score of 0.8. I don't believe this is correct. I think the membership function should be redefined to avoid this or the authors should justify in the text why it should be this way. This problem is avoided for the 'distance' and 'total copy-number' variables.

Line 162 Should also reference figure 5 I believe

167-168. The text here is unclear/confusing. "Confidence scores were then scaled between the minimum score and 100.". This needs to be stated more clearly. It sounds like 0 was mapped to 'the minimum score' (but then what the 'minimum score' is would be undefined). My best guess is that the opposite was done: the crisp scores were linearly mapped with the minimum crisp score mapped to zero and 100 mapped to 100. Can this part of the method be stated more clearly please.

167-168. A more serious question related to this? Why were the confidence scores produced by the fuzzy logic rules subsequently re-scaled at all? This seems to go against the point of defining the fuzzy logic system. The rules, as written, already provided the confidence scores in the range 0-100. As such what OMA reports is no longer the fuzzy logic confidence scores from their system but a re-scaled version of them. It seems like the authors were not happy with the confidence scores returned and so re-scaled them? This should be explained.

Figure 7 are these the fuzzy logic confidence scores or the re-scaled ones?

220. It seems like we don't know that the errors in assignment will be only at the high-end of the range of sequence distances, not also at the low range (e.g. from more recent duplications than the divergence in question)? The text says "we expect there to generally be a low distance between homoeologs", but this is achieved by scaling the membership function to the general range of observed divergence times (Table 2). So the highest confidence for divergence at the initial speciation would be for those in the middle of the range and lower confidence would apply to both those that are older and younger than expected, I would have thought? Perhaps the authors could address this?

227: "would could"


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: ASSIGNING CONFIDENCE SCORES TO HOMOEOLOGS USING FUZZY LOGIC
Review round: 1
Reviewer: 2

Output:
Basic reporting: Glover, Altenhoff, and Dessimoz present a very interesting approach to the issue of homoeolog identification. The use of fuzzy logic to assign confidence scores sheds light on the fact that the identity of these genes is not always known.  This is an important point that would benefit the polyploid community and beyond.

The article has some issues with accessibility in the writing. As a evolutionary biologist who studies polyploidy and does quite a bit of bioinformatics, I found aspects of the fuzzy logic description difficult to follow. Some of this could be easily alleviated by explanation of terms or acronyms (like PAM units, line 150). Another example would be line 158. Clarification of "universe" here would be helpful. Is it the range of input variables? Output variables? Both? The use of "fuzzification" and "defuzzification" throws me off a bit, though I am sure they are perfectly reasonable for use when discussing fuzzy logic. Here, again, a quick definition would be very helpful.
Experimental design: The design is fine but the limitation that these are all younger polyploidy (mesopolyploids) would be useful to be addressed. Since there is a syntenic factor to the confidence score, older events might have fewer identified homoeologs. This potentially limits the scope of use for this approach, though this exact limitation is not test nor mentioned. It would be useful for the authors (probably in discussion) to speculate on these limits.
Validity of the findings: The data/results seem to be very clear with what the authors claim. I especially like that they say that this is not necessarily the best method or schema, but that, based on their manual curation, it is an improvement.

The approach is limited to genomes where the subgenomes are assigned. This is not always going to be possible. The authors acknowledge this.
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 IDENTIFICATION AND EXPRESSION ANALYSIS OF THE MYB TRANSCRIPTION FACTOR IN MOSO BAMBOO (PHYLLOSTACHYS EDULIS)
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: For phylogenetics analysis, it was based on Maximum Likelihood rather than NJ.
Quantitative verification of gene expression levels must employ at least three biological replicates.
Please provide the evidence for selecting SCW-related PeMYB genes. In addition, the authors should provide the lignin content data at the corresponding sampling point.
Validity of the findings: In the materials and methods, the authors mentioned the rice sequences were used for phylogenetics analysis, but there was not any result shown.
Additional comments: The results section contains a lot of discussion content.


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 IDENTIFICATION AND EXPRESSION ANALYSIS OF THE MYB TRANSCRIPTION FACTOR IN MOSO BAMBOO (PHYLLOSTACHYS EDULIS)
Review round: 1
Reviewer: 2

Output:
Basic reporting: the authors should provide raw data and update the reference.
Experimental design: The methods should be described with sufficient information to be reproducible by another investigator.
Validity of the findings: no comment
Additional comments: 1.A phylogenetic tree was constructed with the full-length of MYB amino acid sequences (85 PeMYBs and 132 AtMYBs) to predict the function of moso bamboo and divided into 18 function groups. The authors further depend on the phylogenetic cluster results identified 12 biosynthesis and deposition of the secondary cell wall related MYB genes, this prediction method is too simple and not enough. We know bamboo belongs to the monocotyledonous, perennial grasses, while Arabidopsis is represented dicotyledenous plant. The authors should choose some genes have clear function (including secondary cell wall related genes from different plant, such as grasses plant ) to construct another phylogenetic tree, and according to the cluster result to identify the gene function. This part needs to be strengthened.
2.Figure 1 is not necessary, because I have seen the same figure in other articles. The authors should providing a multiple sequence alignment result (85 PeMYB proteins), and adding some MYB proteins which have a typical characteristic structure from other model pants.
3.Line 63 should insert the reference.
4.Did you repeat when sampling? The sample is single plant or mixed samples? The authors should write clear in Plant Material part.
5.Line 183, What is the concentration of CDNA?
6.Table 1, why does there present two PI，does it mean different analysis content?
7.From line 400 to 402, the authors indicating that these MYBs might play important and central roles in the SCW synthesis pathway, should further analysis the conserved motif, dose these genes shared the same or specific motifs with other PeMYB genes.
8.From line 255 to 257, the authors say Class I including 6 clades (C1, C12, C14, C16, C22 and C32), was responsible for SCW formation by regulating the biosynthesis and deposition of lignin, cellulose and hemicellulose. Class III, including 5 clades (C7, C17, C20, C25 and C29), played important roles in morphogenesis and organogenesis.
In the part of Validation of PeMYBs by using real-time PCR. 12 PeMYBs, including C1, C7, C12, C14, C16, C22, C32, were selected for further validation. Why does only selected C7 in Class III? C12 including 10 PeMYBs, why does only choose two genes? The authors should choose all predicted SCW related genes to validate. I hope the author provides the raw data for this part.
9.The Figure 5 should re-analyse, why does not show * p < 0.05. the gene expression of peMYB64 is not correct.
10.Table S1 should including reference gene primers. If authors use two reference genes, the result will be more reliable.
11.The authors should provide the sequences (gene, cds and protein).


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 IDENTIFICATION AND EXPRESSION ANALYSIS OF THE MYB TRANSCRIPTION FACTOR IN MOSO BAMBOO (PHYLLOSTACHYS EDULIS)
Review round: 1
Reviewer: 3

Output:
Basic reporting: 1.	The English is needeی to improve. This manuscript requires major English language copyediting.

2. Literature references are sufficient and an appropriate background is provided.

3.	In figure 5 the name of font of genes’ names are not clear except PeMYB40. Please, change all fonts same to PeMYB40.

4.	In figure 5, it is better to write “relative expression to PeTIp41” rather than relative expression.
Experimental design: 1. To draw phylogenetic tree, why NJ method was used?

2.	Why PeTIp41gene was used as reference gene?
Validity of the findings: 1. The authors should be clear in the goals of this study. They should also be able to clearly express the novelty and significance of this study in the introduction.

2.	The research aims are well-defined and are relevant. In this study, the authors use meta-analytic statistical techniques and bioinformatics tools to identify and characterize genes in tomato that are differentially expressed during responses to stress conditions. The analysis is based on publically available microarray tomato gene expression data. The analysis meets the appropriate level of rigor and the results are laid out in sufficient detail.

3.	The Conclusion section is minimal, and the authors do not provide a discussion about how their findings connect with the study aims and how their work fits into the larger framework of the related literature. The manuscripts reads too much like a report.
Additional comments: It was explain above.


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 IDENTIFICATION AND EXPRESSION ANALYSIS OF THE MYB TRANSCRIPTION FACTOR IN MOSO BAMBOO (PHYLLOSTACHYS EDULIS)
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
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: GENOME-WIDE IDENTIFICATION AND EXPRESSION ANALYSIS OF THE MYB TRANSCRIPTION FACTOR IN MOSO BAMBOO (PHYLLOSTACHYS EDULIS)
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: 1. It is difficult for me to find author’s change, should present the specific line number where have been revised.

2. The authors indicating that these MYBs might play important and central roles in the SCW synthesis pathway, should further analysis the conserved motif, dose these genes shared the same or specific motifs with other PeMYB genes. The author’s answer is “We have performed further analysis of the conserved motif, but we did not find that they shared the same or specific motifs with other PeMYB genes”. There are no same or specific motifs with other PeMYB genes, I think the answer is contradictory.

3. Arabidopsis should be italic.

4. It will be great if homologous gene related with SCW in model plants or reported researches could be discussed here and comparing with the results of this study.


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

Input:
Title: GENOME-WIDE IDENTIFICATION AND EXPRESSION ANALYSIS OF THE MYB TRANSCRIPTION FACTOR IN MOSO BAMBOO (PHYLLOSTACHYS EDULIS)
Review round: 2
Reviewer: 3

Output:
Basic reporting: 1.	There are three references with the first author Li in 2016, they mud be determined by letter a, b and c.
2.	The reference “Lipsick JS. 1996. One billion years of MYB. Oncogene 13(2):223-235.” Must move before “Liu CW, Fukumoto T, Matsumoto T, Gena P, Frascaria D, Kaneko T, Katsuhara M, Zhong SH, Sun XL, Zhu YM, Iwasaki I, Ding XD, Calamita G, Kitagawa Y. 2013. Aquaporin OsPIP1;1 promotes rice salt resistance and seed germination. Plant Physiology and Biochemistry 63(63C):151-158 DOI: 10.1016/j.plaphy.2012.11.018.”
3.	The reference “Wilkins O, Nahal H, Foong J, Provart NJ, Campbell MM. 2009. Expansion and diversificationof the Populus R2R3-MYB family of transcription factors. Plant Physiology 149(2):981-993 DOI: 10.1104/pp.108.132795.” Must move before “Windham GL, Williams WP, Mylroie JE, Reid CX, Womack ED. 2018. A histological study of aspergillus flavus colonization of wound inoculated maize kernels of resistant and susceptible maize hybrids in the field. Frontiers in Microbiology 9:799 DOI: 10.3389/fmicb.2018.00799.”
4.	The reference “Zhou J, Lee C, Zhong R, Ye ZH. 2009. MYB58 and MYB63 are transcriptional activators of the lignin biosynthetic pathway during secondary cell wall formation in Arabidopsis. The Plant Cell 21(1):248-266 DOI: 10.1105/tpc.108.063321.” must be the last reference.
5.	The English language is acceptable now.
Experimental design: 1.The NJ method is a common method and it is not necessary use maximum likelihood.
2.The replication numbers of experiment is acceptable.
3. methods described well in revised manuscript.
Validity of the findings: 1. The result and conclusion sections was revised and is acceptable now.
Additional comments: References must be listed in alphabetical order


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: DIFFERENTIAL EXPRESSION OF THE GLUCOSE TRANSPORTER GENE GLCH IN RESPONSE TO GLUCOSE AND LIGHT IN MARINE PICOCYANOBACTERIA
Review round: 1
Reviewer: 1

Output:
Basic reporting: This work reports variability in the expression of the glucose transporter gene glcH in cultures of marine cyanobacteria, in response to increasing glucose concentration and to a period of darkness. The manuscript is overall clear and well-written. The findings are interesting and will be useful to the scientific community.  It is however unfortunate that no testing was done in natural environment in order to ground truth findings from culture isolates. I have some concerns about the interpretation of some of the results (detailed below), particularly when using high glucose concentrations in experiments studying a high affinity transporter, and conclusions relating the importance of glucose uptake if transporters expression is down regulated in the dark. Overall the benefits of using sugars uptake for a photosynthetic organism need to be better explained to be more convincing.

The article structure is fine overall, but I found some sentences that should be moved to more appropriate parts of the paper. This would help future readers.
•	The first paragraph in the results section really is methods and should be moved where it belongs. Same for L213 to L218 and L241 to L245. All this information relates to the choice of strains studied, glucose concentrations and incubation times and should be written in the method section in a consistent way. I would also suggest improving the justification related to the choice of strains. Please explain why these strains are best suited to interpret what may be happening in the natural environment.
•	L271 to 274 is also clearly methods, while L266 to 271 should be in the intro.

The figures could be improved. I don’t find it necessary to use different colors for different bars. This is distracting because the colors mean nothing. Choose one color, preferably black or grey. I also recommend combining results per experiment. The glucose concentration experiment with Prochlorococcus (fig. 1, 2, 3 and 4) should become figure 1, the glucose concentration experiment with Synechococcus (fig 5 and 6) should become figure 2, and the dark experiment (fig 7 and 8) should become figure 3. That would make it easier to compare results for different strains in the same type of experiments. Why are there no error bars for the controls: how that affects statistical analyses?

While sufficient field background/context is provided, the authors self-cite too many times throughout the manuscript and overemphasis their previous work in sentences such as “previous results from our team” (L55), “by our team” (L151, L157), “our team” (L302), “results from our group” (L387); or “we proposed” (L307), “we showed” (L313), “we performed” (L316) while references cite a first author that is not a co-author to this manuscript. In my opinion, scientific publications should not be an advertisement for a research group, even leaders in the field. I therefore recommend removing those mentions to the group or team and simply refer to the publications. Same goes to statements about their ongoing and future work (L384 and L460-462): this should be removed.

L78-80: The authors refer to Muñoz-Marín et al. 2013 but this paper does not demonstrate that the uptake of sugars is beneficial in terms of bioenergetics in comparison to CO2 uptake. This needs to be demonstrated because this statement is core to the work presented here.
Experimental design: The introduction clearly raises important research questions and states how the present work fills an identified knowledge gap.

Overall the experimental design is sound. I have several questions though.
•	In the introduction, the authors state that sugars concentration in the ocean are very low: please provide ranges and references. Also explain why the chosen concentrations of 100 and 1000 nM glucose would be relevant to natural ecosystems. This is puzzling considering that the authors make the case that they are studying a high affinity transporter.
•	As highlighted above, I am questioning why there was no replication of the control (no error bars in the figures. Or do the error bars for the different treatments consider the variability in the control (i.e. did the authors calculate the treatments standard deviations taking into account the standard deviation in the control).
•	It would have been important to test if the addition of glucose to a dark treatment would result in increased expression of glcH. I think it would have been very informative and complimentary to the experiments with glucose additions in the light. Also, L385-387: is it because the cells died under darkness? Or maybe they shut down their metabolism until light is restored? Did you test if glucose uptake is restored after switching cells from dark to light? Indeed, the big question that rises from the authors findings is what is the advantage of using glucose as a source of carbon if the uptake is so low/inhibited in the dark? For a microorganism that has the machinery to do photosynthesis, the ecological advantage to keep the machinery for glucose uptake is unclear if they can benefit from it mostly where/when light is available. I think this is an important point that needs to be better explained in the paper.
•	Please justify the choice of 24h of incubation.
Validity of the findings: The results are overall nicely interpreted and put in context. However, the interpretation of the results for incubations in the dark need to be more carefully assessed. For example, in the discussion L344-347, the authors argue that mixotrophy in marine cyanobacteria could be more useful under natural low light conditions. But to me this is contradictory to the result that glucose uptake is reduced under darkness. It is important that the authors improve the discussion related to this hypothesis and their findings.

L227-228: Please be quantitative in this statement. Considering variability in gene expression at 1000 nM for SS120 and MIT9313: is the difference between strains different?

L239-240: Please be quantitative

Paragraph L348-355: Why would glucose concentration be lower in coastal than in open ocean? Please provide data (if not glucose, at least sugars concentration) and references from the literature to support this hypothesis.

L372-376: Interpret the fact that the high affinity glcH is upregulated in response to relatively high glucose concentrations: 100 to 1000 nM are very high for a high affinity transporter that should 1) saturate at relatively low concentrations and 2) never be exposed to such high concentrations in the natural environment.

L411-413: Could this be an indirect effect of glucose addition?

L451: What metabolic needs? If DIC is not limiting and glucose uptake reduced when photosynthesis is reduced, what is the advantage of sugar uptake? Improve explanation related to this important point throughout the manuscript.
Additional comments: L121: growth media for Prochlorococcus and Synechococcus are very different: particularly important is the fact that Prochlorococcus was grown on natural seawater (where was it sampled?) containing sugars while Synechococcus was grown on artificial seawater (no sugars). Can that affect the results?
L136: Why using different absorbance wavelength?
L78: I recommend adding more recent references.
L299: Please define Ks
L330 and L430: Should be “The results presented here”
L333-337: Please remind the readers which strains are LL or HL. That would help non-experts.
L360: Please interpret this observation
L434: Also explain their results with glucose addition because this is relevant to your 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: DIFFERENTIAL EXPRESSION OF THE GLUCOSE TRANSPORTER GENE GLCH IN RESPONSE TO GLUCOSE AND LIGHT IN MARINE PICOCYANOBACTERIA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript titled ‘Differential expression of the glucose transporter gene glcH in response to glucose and light in marine picocyanobacteria’ by Moreno-Cabezuelo et al, details the differential expression of the glucose transporter gene glcH in response to glucose and light conditions in marine picocyanobacteria (Prochlorococcus and Synechococcus). Authors have analyzed the transcriptional regulation of glcH in varying glucose concentrations and light conditions by qRT-PCR in four Prochlorococcus and two Synechococcus strains. This work is purely an extension of previously reported work by the authors.

As author has complemented the major questions in their earlier publication, I think their data of transcriptional expression profile was a big missing link in their earlier report, which here will be well-complemented and major advancement for the field.
Experimental design: The background and introduction are appropriate and relevant. Sufficient information about the previous findings is presented for readers, which is helping to follow the present study rationale.
The methodology is well executed, and authors had provided details of growth and culture conditions, in which different Prochlorococcus and Synechococcus strains were grown. However, authors didn’t provided detail of the difference in absorbance units of the starting culture for the two sp.
Validity of the findings: The results seem to be valid but not well elaborated. The first paragraph of result section is mostly the repetition of method section. The clades discussed in lines 203, 205 and 206 should be clearly described in the phylogenetic tree, as also reported in Muñoz-Marín et. al. 2017. I would suggest writing ‘Results’ and ‘Discussion’ together.

Lines 70-72 and Lines 90-92, reference should be incorporated.
Line 124, it should be either “as described earlier” or “in El Alaoui et al. 2001”
Lines 229-234, 239-240 and 243-245 consider rephrasing to make the message clear.
Line 298 elaborate Ks for e.g., Ks (Saturation constant)

I have major concern with discussion as it contains a lot of background information, which has already been discussed in introduction. Due to which, the major impact of this manuscript is hidden. For example, authors had discussed about the identification of GlcP and melB/glcH gene in the first paragraph of discussion and in the second paragraph demonstrated the work performed by their group on glcH in earlier studies, which has been done in the introduction too.  Thus, the part of discussion that is the repetition of introduction should be omitted which will help to improve the discussion.

Figures can be clubbed together as different part of same figure. By which it would be easy to compare the two profiles. For example, the graphs representing the effect of glucose concentration in different strains of Prochlorococcus, Figures 1-4 should be combined together as Figure 1A, 1B 1C and 1 D.  It stands true for Synechocystis sp. i.e., Figure 5 and 6 should be combined as Figure 2A and 2B. Then, Figure 7 and 8 will be Figure 3 and 4, respectively.

Figure legends are poorly written and basically same for each figure. Author need to describe more about result presented in each figure legend.
Additional comments: As authors have presented the qRT-PCR data to investigate the transcriptional expression profile of glcH genes, it would be more convincing if authors would have also checked the regulation at protein level. Comparative western blotting analysis of the proteins corresponding to these genes would be the ultimate data to look upon the physiological regulation of GlcH in the observed conditions.

The manuscript should be rewritten with more focus on the findings of the current study. I have found serious issues with writing of this manuscript, thus the manuscript needs to be well written and well organized prior to be considered for publication.


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

Input:
Title: DIFFERENTIAL EXPRESSION OF THE GLUCOSE TRANSPORTER GENE GLCH IN RESPONSE TO GLUCOSE AND LIGHT IN MARINE PICOCYANOBACTERIA
Review round: 1
Reviewer: 3

Output:
Basic reporting: no comment
Experimental design: The research question is well defined and performed well.
Validity of the findings: FIndings of research are well discussed with the inclusion of data and conclusions from other peer researchers.
Additional comments: I thank the editor for providing an opportunity to review article “Differential expression of the glucose transporter gene glcH in response to glucose and light in marine picocyanobacteria”.

This article can be accepted for publication after addressing comments below.
1.	Interesting work showing the effects of glucose and light on the expression of glcH, however, there is no genetic data to support this conclusion. The author should also test whether or not expressions of other genes are affected and if those changes contribute to bacterial fitness? After taking glucose inside. This will increase the impact of the MS.
2.	Please reduce the introduction and discussion part. It’s quite long and unfocused. Discussion part includes mostly about previously published work from the same lab rather than focusing on results in this manuscript.
3.	Manuscript figures should be organized in only two figures. As discussed in result section figure 1 should be about glucose uptake and its effect on glcH expression profile across strains. And figure 2 should be the effect of light on glcH expression. There is no meaning of having figures in such a split manner. It creates a distraction. Please consolidate figures.
4.	When there is a higher amount of glucose, some strains increase glcH expression, which supports the idea that more transporters could facilitate higher glucose uptake. However, at the same time, transcriptional up-regulation would lead to utilization of more cellular energy. How bacteria make a decision when we think in terms of cellular energy homeostasis? Please discuss.
5.	Could you comment on GlcH transporter protein in different bacteria? Uptake ability varies in different strains, is it possible that it is due to protein conformation or sequence differences? Is it possible to do protein alignment for glcH in difference strain to understand similarity and difference across species?
6.	Authors also pointed out that possible Hik31 kinase sensing mechanism involved for sugar uptake, when it present in the outer environment, that leads to transcriptional up-regulation of GlcH transporter and higher uptake. Could you elaborate pathway from sensing to transcriptional regulation mechanism?


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: DIFFERENTIAL EXPRESSION OF THE GLUCOSE TRANSPORTER GENE GLCH IN RESPONSE TO GLUCOSE AND LIGHT IN MARINE PICOCYANOBACTERIA
Review round: 2
Reviewer: 1

Output:
Basic reporting: The manuscript has improved in clarity, it is better organized and easier to follow. The figures are also much better.
Experimental design: Thanks to the manuscript reorganization, the experimental design is much easier to follow. It is now clear.
Validity of the findings: I have nothing to add in comparison to my previous review. The authors have answered my concerns.
Additional comments: The authors have answered my questions and revised the manuscript accordingly. I am satisfied with their answers and with the current version of the manuscript.


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

Input:
Title: DIFFERENTIAL EXPRESSION OF THE GLUCOSE TRANSPORTER GENE GLCH IN RESPONSE TO GLUCOSE AND LIGHT IN MARINE PICOCYANOBACTERIA
Review round: 2
Reviewer: 2

Output:
Basic reporting: The article “Differential expression of the glucose transporter gene glcH in response to glucose and light in marine picocyanobacterial” by Moreno-Cabezuelo et al.  contain interesting and relevant findings for the field.
Introduction section is well executed and is clearly describing the background information as well as the objective for the current study.
Materials & methods section has improved a lot and is providing most of the necessary details in the revised manuscript.
Result section is nicely interpreted and more focused on the current findings in the revised manuscript. However, discussion still is quite long, and authors should work on making their article balanced, yet informative.
Figures are much organized and easy to follow in the revised manuscript which has improved the quality of revised manuscript. However, the language used for the figure legends are still sounding repetitive.
Experimental design: The design of experiments is well plotted and well executed by the authors.
Validity of the findings: The findings of the study are novel. These are clearly explained, discussed and well supported by the previous findings.
Additional comments: Overall the manuscript is providing an important and novel piece of information which will be utilized by the scientific community. Figure legends are repetitive and hence are not acceptable in the current version. Authors need to rewrite the figure legends and should avoid the redundancy in language.


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: DIFFERENTIAL EXPRESSION OF THE GLUCOSE TRANSPORTER GENE GLCH IN RESPONSE TO GLUCOSE AND LIGHT IN MARINE PICOCYANOBACTERIA
Review round: 2
Reviewer: 3

Output:
Basic reporting: clear and focused
Experimental design: defined question and experiments related.
Validity of the findings: results are discussed well.
Additional comments: I thank the editor for providing an opportunity to review article “Differential expression of the glucose transporter gene glcH in response to glucose and light in marine picocyanobacteria”.
Authors have incorporated and addressed all comments and suggestions. The manuscript is improved and consolidated. I recommend this article to be accepted for publication in PeerJ.


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: DIFFERENTIAL EXPRESSION OF THE GLUCOSE TRANSPORTER GENE GLCH IN RESPONSE TO GLUCOSE AND LIGHT IN MARINE PICOCYANOBACTERIA
Review round: 3
Reviewer: 1

Output:
Basic reporting: The revised form of manuscript is much refined and it is now easy to follow. Hence, the manuscript can be considered for publication.
Experimental design: The experimental design is well executed.
Validity of the findings: The findings are clearly explained and discussed.
Additional comments: I recommend this article to be accepted for publication in PeerJ.


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: DIFFERENT REVEGETATION TYPES ALTER SOIL PHYSICAL-CHEMICAL CHARACTERISTICS AND FUNGAL COMMUNITY IN THE BAISHILAZI NATURE RESERVE
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper have an important comparison of fungi community structure in different types of re-vegetation forests. Even with the limitation of replicates (three for each kind of re-vegetation forest) the author showed a big difference in fungi communities among the places. However their conclusion about re-vegetation types been the strong factor determine fungi composition was not explicit tested, other factor as bacterial composition or soil treatment was not discussed.
Experimental design: More explanation is needed about the soil collection, the authors said that they collect 15-20 sub-samples in each plot but not explain how these points were selected. Also they do not explain why the variation 15-20 sub-samples. Furthermore the analysis are badly explained, with confusion about software and packages, poor description of methods (e.g. which dissimilarity matrix was used in NMDS analysis) and no referenced. The author need re-write this part with more details, correct use of packages and software and cite the author that have a big work creating these tools.
Validity of the findings: The finds were interesting, however many test with many variables were conducted with very little replicates. I understand that all studies have sampling design limits but the author need at least discuss these limitations.
Additional comments: The study is nice, but the writing need to be improved, the analysis need to be re-write with detail and clarity and the discussion need to access the limitation of the study.


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

Input:
Title: DIFFERENT REVEGETATION TYPES ALTER SOIL PHYSICAL-CHEMICAL CHARACTERISTICS AND FUNGAL COMMUNITY IN THE BAISHILAZI NATURE RESERVE
Review round: 1
Reviewer: 2

Output:
Basic reporting: Basic reporting: In this work Deng and collaborators evaluated the effects of different revegetation types on soil physical-chemical characteristics and fungal community in the Baishilazi Nature Reserve using ITS rRNA Illunima Miseq high- throughput sequencing. I commend the authors for the excellent experimental design and extensive data collection. Unfortunately, the paper suffers greatly from poor language usage. Please pay special attention to grammar and syntax of the manuscript. There are several parts in the paper that need almost complete rewriting. I strongly suggest using an English language editing expert individual (English native speaking) or use a relevant commercial service.

In addition, the discussion needs to be improved as well. I suggest the authors to further examine former similar work and to interpret their results in terms of the impact of different revegetation types on the fungal community, as this section of the paper seems to be merely descriptive and lacks interpretation of their results (from ITS sequencing, soil physicochemical properties, and revegetation types). Also, several diversity indexes were calculated, and not appropriately considered. Why did you choose to estimate alpha diversity indices such as Chao1, ACE, Shannon, and Simpson? What distinctive traits of the community may be evaluated through each of these? Please explain in the methodology and review in the discussion.
Experimental design: Experimental design: The experimental design and the methods are acceptable for the most part. However, the appropriate software citation is lacking (Data Analysis, lines 145-148). Please include proper citation for QIIME, including the used version. The same for R, including the name (and proper citation) of the used packages.
Validity of the findings: Validity of the findings: I feel that the authors made appropriate conclusions for their work. However, it seems that ITS sequences were not deposited in a relevant database, and hence are not publicly available. According to the guidelines of PeerJ this is mandatory for publication. Besides, data availability is indispensable in order to ensure the reproducibility this investigation, and very helpful for future works. So, the authors are urged to provide accession numbers for their dataset, demonstrating its availability in a public relevant repository.
Additional comments: Comments for the author: This manuscript adds important and interesting information to the knowledge of soil fungal communities and their response to environmental fluctuations. The investigators in this paper did an exceptional amount of work that I feel should be mentioned. The science and conclusions appear sound and are interesting. However, before being considered for publication I feel that the manuscript needs to be importantly improved in English language usage, and carefully revised for careless errors (some examples include capitalization mistakes e.g. 10th line of the abstract, misspelling of Pearson statistical index, among several others). Also, as explained above, the discussion needs to be improved in order to enhance the contribution of this work. Lastly, it is crucial for the authors to make their datasets publically available.


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: DIFFERENT REVEGETATION TYPES ALTER SOIL PHYSICAL-CHEMICAL CHARACTERISTICS AND FUNGAL COMMUNITY IN THE BAISHILAZI NATURE RESERVE
Review round: 1
Reviewer: 3

Output:
Basic reporting: Comments for the manuscript entitled “Different revegetation types alter soil physical-chemical characteristics and fungal community in the Baishilazi Nature Reserve”. The authors investigated the relationship between soil fungal community composition and soil properties to five re-vegetation areas with different dominant species (JM = Juglans mandshurica, QM = Quercus mongolica, CB = conifer-broadleaf forest, LG = Larix gmelinni, PK = Pinus koraiensis) at the Baishilazi Nature Reserve in the mountainous region in China.
It addresses one objective- to relate the soil fungi community composition with the type o re-vegetation- specifically, shifts in the abundance and composition of soil fungal communities to changes in soil properties.
The authors found interesting patterns for the relationship between soil fungi community composition with the type of re-vegetation, but some methodological aspects are unclear some. For example, What do they mean with available nitrogen, ammonium plus nitrate? and What technique did they use to determine available phosphorus or instruments to determine the soil total carbon?. How did they determine diversity or calculate the overall index? The above makes the interpretation and scope of results difficult to understand.
In general, the manuscript shows interesting data and results. It is relatively well written, although the verb conjugations and several details could be examined. The authors can improve the material and methods section. Also, it is very important to highlight that the plant-soil-microorganisms relationships are feedback relationships and it is difficult to determine the cause-consequence.
The introduction shows a good theoretical context, and the literature is relevant. The methods were not described with sufficient detail.
Experimental design: The research objective is well defined and it is relevant. The experimental design seems adequate, however the analysis of the relationship between soil properties and diversity of the fungi community could be improved for better results.
Validity of the findings: The analyses between diversity and soil properties can be improved if instead of the Pearson´s rank correlation coefficients (Table 4), an analysis of main components (PCA) was made with the set of soil properties and vegetation types. Also, regression analysis could be done with the resulting scores of the PCA.  Where, the response variable would be each diversity index and the independent variable would be the analysis score of PCA.
Additional comments: L35-37 In sentence “Our results suggested that coniferous forest (LG, PK) and conifer-broad forest (CB) had reduced soil total C, total N, and Available N compared with broad-leaved forest (JM, QM)”, “Available N” should be “available N”.

L37-38 List of index could be as “Shannon, ACE, Chao 1 and Simpson index” instead of “Shannon index, ACE index, Chao 1 index and Simpson index”.

L44-46 In the sentence “The results of canonical correspondence analysis (CCA) shown that the soil environmental factors, such as soil pH, total C, total N, available N and available P had greatly influenced on the fungal community structure.”, “shown” should be “showed”.

L78-80 “work” should be “studies”
L81 “Different” should be “different”
L82 “Directly”, could be “Specifically”
L83 “nutrient” should be “nutrients”
L84-86 “was” should be “were”
L106-107 Are the symbols in the geographic coordinates correct?
L108 I do not understand the “hm2” units
In “Site description”, information about soil type according to the FAO classification is missing.
In “Material and Methods” section, information about determination of soil properties variables and diversity index calculation is missing.

L160 It is important to mention that the authors refer to nitrogen and available phosphorus, so it is necessary to include the analysis description of soil properties in the materials and methods section.

It is advisable to add a space between the values and the units that are reported in the results section and in all manuscript.

The discussion section can be improved if values of eco-physiological characteristics of plant species are included to understand the possible routes of their relationship with soil properties.

L262-263. Alkaline soil? Soils are very acidic, alkaline would be close to a pH of 8
L263-265. It would be advisable to add references
L270-272 It would be advisable to add the biological or ecological meanings of these relationships with the diversity index.
L279. It is recommended to remove the "and" for the best understanding of the idea.
L281 What do the authors mean with “their history of evolution”?

The analyses between diversity and soil properties can be improved if instead of the Pearson´s rank correlation coefficients (Table 4), an analysis of main components (PCA) was made with the set of soil properties and vegetation types. Also, with the resulting scores of the PCA, regression analysis could be done, where, the response variable would be each diversity index and the independent variable would be the analysis score of PCA.

Table 1 can be improved if the authors change “Types” in column #1 to something like “Vegetation types” or “labels of main species in re-vegetation areas” , and “Dominant Vegetation” to “Dominant species”, in “(m)” they could include “(m above sea level)”, and “Forest Type” to “Forest type”. The note at the end of the table can be place in the table description.

Table 2 can be improved if the authors use the same units for the total elements (g / kg) and for the available ones (mg / kg). The note at the end of the table can be place in the table description or (see table 1 for abbreviations).

Figure 5 does not seem very clear to me, but I am not an expert in the interpretation of this tool. I do not understand what the authors refer to "the relative abundance of the top 50 generates identified in the bacterial communities of the soils".


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: DIFFERENT REVEGETATION TYPES ALTER SOIL PHYSICAL-CHEMICAL CHARACTERISTICS AND FUNGAL COMMUNITY IN THE BAISHILAZI NATURE RESERVE
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors improved the language and explain better methods and results, however there are yet problems in these sections. There are problems with reference style, the wrong citations, results showed without methods be presented (e.g. Principal Component Analysis line 201). The authors use a lot the word "significant" without show any test. Also the replicate are very limited, 15 plots in the total, and there is a high number of test. For instace, in the table 4, if Bonferrone correction was applied the significance level might be of p < 0.0017 (alpha/number of tests). The fifures 12 - 16 are repetitive of figure 1, and not cited in the text.
Experimental design: The experimental design is limited (three replicates for each revegetation type, 15 plots in the total), however it is hard have a good replicate number. I recomend the author, due the limitation of replicates, avoid multiple test, such as 4 different diversity index. Methods are yet with problems. There is confusing in the place where the analysis should be provided. There is no description of PCA in the methods, the dissimilarity index used in the NMDS just appear in the results and there is wrong way to cite reference (e.g. R software, that should be in this way - R v3.3.2 (R Development Core Team, 2017)). Title of figure 2 is wrong, there is Principle and the correct is the Principal.
Validity of the findings: The main problem of the valit of the findings is the replicate number. The results are sometimes dense and the discussion is a little confuse due the language. For exemple: "The composition of fungal community in terms of phyla and genera did not significantly differ among the different revegetation pathways, although the relative abundance values varied, probably as a result of different root residues and secretions produced by different tree species (Degrune et al., 2015). Although our research is limited due to the low number of replicates (three for each kind of revegetation forest), significant differences in fungal communities among different revegetation types were observed[But no difference in fungal composition, it is confuse, please explain better.]. " I couldn't understand what was different and what was not, more explanation is needed. Also the author use a lot the word "significant" when no test was performed or presented.
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: DIFFERENT REVEGETATION TYPES ALTER SOIL PHYSICAL-CHEMICAL CHARACTERISTICS AND FUNGAL COMMUNITY IN THE BAISHILAZI NATURE RESERVE
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors have done a good job revising the manuscript, and have addressed all my previous suggestions. For this revised version, I have a few comments in relation to figures and tables and their legends:
•	Figure 1: Letters A and B in red are very hard to read. Please edit the image in order to improve this problem (or perhaps change the color, the font, or even add a shade).
•	Figure 4: Revise the use of italics. The label “other” should not be in italics.
•	Figs. 7 and 9, where genus names should be written using italics.
•	Please revise careless typos in figures labels. For example, missing spaces before “%” of the y-axis in Figs 4 and 5; and before the parenthesis in Fig. 10 (both axis).
•	Figure 9: It is not mentioned what does panel “A” and “B” represent. Also, some labels (letters), corresponding to fungal taxa are jumbled (and therefore, difficult to read).
•	Tables 2 and 3: It is not mentioned what does the letters (a, b, and c) after the values represent.
•	Table 5: Legend “Person’s rank correlations between the relative abundances of dominant bacteria groups and available edaphic factors” does not correspond to the table, as this table presents fungal data as well.
•	Panels in Figure 1 are not mentioned in the manuscript (within the text).
•	Are files: peerj-30722, peerj-30722-File_2, peerj-30722-File_3, peerj-30722-File_4, peerj-30722-File_5 supplementary material? These are not mentioned in the manuscript. If they are intended as supplementary material pleas include a legend for each.
•	It is desirable that the authors complete the information presented in Tables (peerj-30722-File_2, peerj-30722-File_3), with the following data (one line per sequence): Culture name, site
3, date of sampling, the result of best blast hit: species name with % of identity for the best coverage, species name retained in the present study.
Experimental design: No comments.
Validity of the findings: No comments.
Additional comments: The manuscript has greatly improved, I acknowledge the authors for their great effort. In principle, this study is relevant and expands knowledge. However, I still consider that it could be presented better. Particularly, redundant figures could be removed (e.g. Fig. 1 and Figs 11-16 are showing the same thing; I also feel that not all the barplots on the diversity results at a genus and phyla level are necessary as they don't add significantly to the information, so some of them could be moved to supplementary?).


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: NETWORK MODELS OF DRIVER BEHAVIOR
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article is well-written, with a clear structure and relevant citations. The scientific background is extensive, with sound theoretical considerations on why the network model can be interesting within the context of driver behavior.
The raw data are available and the figures are clear. However, the author could expand some more on how he came up with the relationships within the hypothetical network model of traffic behavior from figure 2 (are they based on anything else than the relationships in figure 1?).

The paragraph from line 77 can be a bit confusing at some points when looking at figure 1. Some of the (problematic) theoretical assumptions and conclusions explained in that paragraph seem more related to one-factor common cause models than to latent variable models in general. I find that these problems from a latent variable perspective and the problems from a one-factor common cause model are sometimes mixed up within the manuscript. The latent variable view of violations and errors from figure 1 already seems more expanded than the one-factor common cause models being used in latent variable models for psychopathology or intelligence, where the assumption is that all observable scores (from an IQ test or all depression symptoms) are caused by only one latent variable. Therefore, I don’t fully agree with the author that all assumptions described in this paragraph hold for the model of figure 1– for example the assumption that the variation in the observed items can only be explained by variation in the latent variables ‘violations’ or ‘errors’, or measurement error, since the latent variables themselves are influenced by some other higher-order (latent) variables (called “background factors”).
However, there are more specific problems related to latent variable models which do relate to the model in figure 1 and are very well described, such as the problem that the model of figure 1 doesn’t allow direct influences between the observable variables and gives no direction for interventions. Personally, I would suggest the author to describe the more specific problematic assumptions related to the latent variable view of violations and errors (figure 1) and to use the fact that this model already is quite an extensive model from a latent-variable perspective as a way to enucleate the urge for a model that accepts direct interactions, such as network models. This is a minor revision to clarify the text without altering the scientific relevance of this study or the conclusions.
Experimental design: The experimental design of the analyses is very well described, making it understandable for the reader what the author has done and with what intentions. The methods are described with sufficient detail. The study seems easily replicable, with freely available data and clear and comprehensible R-code. The most important statistical results are and well interpreted.
One minor revision would be to better explain the difference between the ‘cross-sectional network’ and the ‘between-person network’. Although the author is right in the difference between these networks and correctly citing the paper by Epskamp, Waldorp, Mottus & Borsboom (2018) where these distinct networks are introduced, they are introduced within the context of time series networks. Without more explanation, the name of these two types of networks are confusing, since normally between-person networks are based on cross-sectional data.
Validity of the findings: The conclusions are well stated and linked to the original research question. The discussion is extensive with good suggestions for future research. I agree with the call of the author for future research regarding forming a theoretical network model of driver behavior, however, applying the network model to empirical data of driving behavior is a very nice first step for the field.
One suggestion for the network comparison is to include a figure where the networks are plotted in the same lay-out, to better see the differences between them.
Additional comments: This is a well-written manuscript, with an original application of network theory. I recommend this manuscript for publication with minor revisions.


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: NETWORK MODELS OF DRIVER BEHAVIOR
Review round: 1
Reviewer: 2

Output:
Basic reporting: 1) The manuscript could benefit from a thorough double-check of its structure. For example, information about analyses is sometimes scattered throughout the methods and results section. In particular, the current structure of the “Measures” (L. 158-175) section could be improved, because it includes information that should be given in the “Statistical Analyses” section (e.g., which items were used in which analysis) and information that should be better given in a “Procedure” section (e.g., the fact that the “Learning to drive questionnaire” was administered before the DEQ).
In the materials section, please simply provide a list of all instruments and, for each instrument, a list of all constructs assessed by it, with an example of item for each.
Experimental design: 2)	L. 158-175. Why using different subsets of items in different analyses? For example, only a subset of 31 DBQ items was included the network analysis, whereas more items were included in the regressions. The choice of omitting an item from an analysis is very important and should be justified accordingly.

3)	L. 152-157. I could not understand the exclusion criteria. “Cases with non-missing data in all variables were included, resulting in a sample size of 8858.” How did these 8858 respondents become 1173 and then 1152, if they did had no missing data in all variables? Furthermore, since the differences between the two final sample sizes (N = 1173 vs. 1152) are very small, it might be useful to use the same sample of 1152 for all analyses. This would guarantee that all differences observed between the two networks are due to the introduction of extra variables, and not to the slightly different samples considered.

4) L. 129-130. The between-person network does not represent “differences between drivers”, but the dynamics involving the typical levels of a trait (Costantini et al., 2017) (see also L. 257-258). The authors present a between-person network computed by averaging data across four timepoints and a cross-sectional network computed by using only the first timepoint. However, the cross-sectional network is also a between-subject network which however uses only one timepoint instead of four to estimate the DEQ variables. My suggestion would be to consider a single between-subject network in which DEQ variables are estimated as the average across the four timepoints, whereas the variables assessed only once (e.g., sex, attitude etc.) are included in the network as they are.

5)	Why performing tuning parameter selection using EBIC for network analysis and Cross-validation for regression analysis?

6)	Given the longitudinal nature of the data, why not considering also a within-subject network (Costantini et al., 2017), informing on the relationships among violations/errors within occasions, after controlling for each driver's typical beahvior? This would be more in line with what is stated in the discussion section (e.g., L 438-453)

7)	L. 179-181. Why choosing a subset of background factors, when the network estimation method includes a lasso regularization that allows performing predictor selection automatically?
Validity of the findings: no comment
Additional comments: There are many strengths in this manuscript, such as the use of state of the art methods such as network models and regression with tuning-parameter selection, to model a socially-relevant phenomenon such as driving behavior. Furthermore, I agree with the authors that the network approach is particularly suited to model this type of behaviors, which are arguably causally interconnected. In sum I found the manuscript very interesting and I think that it is should be published.
 However, I also think that the manuscript may benefit form a careful revision in its structure (as I detailed in the Basic Reporting section). Furthermore, several methodological choices need a stronger justification (as i detailed in the Experimental design section). I also have a few general comments, that I present here in order of importance:

8)  I think that a limitation of this study is that psychological variables other than those directly related to driving were not considered. General psychological characteristics (e.g., impulsiveness and low conscientiousness, attention, memory) might explain part of the relationships identified in this study. A potential future development of this study could involve assessing these variables and inspecting their role within the network. I expect that some of these variables might explain some of the relationships emerged in this study. Notice that this would not be the same as hypothesizing abstract "latent" variables based on driving behavior alone (e.g., violation proneness) and that it would be therefore compatible with a network approach, both theoretically and methodologically.

9)  L 61-116. The latent-variable models are represented in a simplistic way and perhaps overly criticized in the introduction. For example, albeit Reason et al. (1990) have considered only a model with two latent variables, one could have opted for a more complex Structural Equation Model (SEM) including a larger number of latent variables and path relations among them, to represent complex relationships. Furthermore, the causal interpretation of latent variables is not the only possible one, e.g., they can be considered statistical summaries that are useful for several practical purposes. When presenting latent variable models, it could be useful to consider also some of their strengths (e.g., they provide simple models and simple assessment procedures). In sum, I think that the point should not be that latent variable models are flawed, but that network models can provide additional information. Although network models allow representing relationships that cannot be well modeled by SEM alone, this does not mean that latent variable models cannot be also useful (e.g., see Epskamp, Rhemtulla, & Borsboom, 2017).

10) L. 118-125. Other possible interpretations of a nonzero edge include the presence of an unmeasured (latent) variable affecting both nodes (Epskamp, Kruis, & Marsman, 2017) and the inclusion of a common “collider” (i.e., a variable that is caused by two variables) in the model (Epskamp, Waldorp, Mõttus, & Borsboom, 2018; Lee, 2012).

11) L. 236-243. Why not considering also a lasso regression model, consistent with network estimation?

12) L. 256-257. What it is meant by “The results reported below are based on the maximum number of cases available for the respective analyses”?

13) L. 388-389. Please, specify that the node is the most central only according to closeness. It would be useful to specify that the success of the intervention would depend on the assumption that the centrality of the node reflects causal connections emanating from that node.

Minor comments:
- L. 34. Please, provide reference for the DBQ when first mentioned.
- L 43-49. The three quotations by Reson et al. (1990) are somehow redundant. Please, summarize them in a single sentence.
-L. 140-150. Please clarify the longitudinal nature of data, I understood that the data were not cross-sectional only when reading L. 182.
- L. 237. For consistency, use GCVE instead of “deviance statistic”.
- L. 244-247. It would be useful to specify that model fit was computed on the validation data (N = 288).
- L. 236-243. The letter lambda was used to indicate the lasso parameter for networks and the ridge regression parameter for the regression analysis, whereas in regression analysis alpha is used to indicate the lasso parameter. Would it be possible to use a different notation (e.g., using lambda always to indicate lasso penalty) to avoid confusion?
- L. 348. Please, specify “parsimony” better. How many parameters did each model include?
- Figure 1. Why including predictors only for Violations in the example?
- Figure 2. Why including congestion and stress, which are not in Figure 1?