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: SOCIAL NETWORK COMMUNITY STRUCTURE AND THE CONTACT-MEDIATED SHARING OF COMMENSAL E. COLI AMONG CAPTIVE RHESUS MACAQUES (MACACA MULATTA)
Review round: 1
Reviewer: 1

Output:
Basic reporting: The study investigates patterns of commensal E. coli strain sharing in relation to individual, social and community characteristics in 3 captive-housed group of Rhesus macaques, a social non-human primate. Commensal E. coli genetic diversity in subtypes or strains is extracted from feacal swabs and obtained through multiple cultures and DNA fingerprinting procedure. Social networks are built from observations of behavioural interactions during 6 weeks. The study concludes at a significant effect of group membership and of social community (based on social network clustering analysis) on the % of similarity between E. coli subtypes, and a lack of a significant effect of age, sex, matriline membership and dyadic interaction frequencies.
Overall, the study is well-designed and has the potential to be of major significance for animal epidemiology. (There is always a) But the writing is quite verbose; the introduction and discussion are a bit long-winded; and there are many repetitions throughout the text (and quite some typos). This makes for a lengthy read where the reader loses focus rapidly. I also find that the introduction could be punchier by delving right away into epidemiology, transmission, infection, and linked social processes, instead of too much advocating for social network analysis tools and describing what others did or did not do. An on-point straightforward presentation of the state-of-the-art and objectives of the study would be more interesting. This is also the case for the discussion. Specifically, I don’t think that nowadays we can say that “conventional epidemiological assessments of infectious agent acquisition often assume, or treat the probability of contact for every pair of individuals in a population as equal” lines 71-72 so the authors might want to jump right in the nowadays state-of-the-art and rather insist on the level of resolution microbial genetics offer for tackling our questions. Paragraph starting line 98: the authors might also want to mention that E. coli expresses enough genetic diversity to be able to build individual host genetic profile with enough between individual variability (see Craft, M. E. (2015). Infectious disease transmission and contact networks in wildlife and livestock. Philosophical Transactions of the Royal Society of London, Biological Sciences, 370(1669), 1–12. http://doi.org/10.1098/rstb.2014.0107).
Furthermore, there are some decisions made by the authors with regards to thinking or methodology that only appear clear in the discussion whereas they would have their space in the introduction or methods already (for instance, lines 480-484 could support the assumption that environmental contamination is low and so any sharing might be attributed to x,y,z instead, either in the intro or method; or lines 544-550 about group III social instability).
I am also missing a short paragraph about the significance of the study not only in terms of epidemiology and captive population health management but also on more fundamental questions such as social processes and evolution or host-parasite interaction and evolution. This would give a bit more meat to the article.
Finally, in general, the study is well referenced but some important ones are missing, for instance see above Craft 2015 as well as other reviews more accessible than a book chapter like: Godfrey, S. S. (2013). Networks and the ecology of parasite transmission: A framework for wildlife parasitology. International Journal for Parasitology. Parasites and Wildlife, 2, 235–245. http://doi.org/10.1016/j.ijppaw.2013.09.001
Rushmore, J., Bisanzio, D., & Gillespie, T. R. (2017). Making New Connections: Insights from Primate–Parasite Networks. Trends in Parasitology, xx, 1–14. http://doi.org/10.1016/j.pt.2017.01.013
Schmid-Hempel, P. (2017). Parasites and their social hosts. Trends in Parasitology, 33(6), 453–466. http://doi.org/10.1016/j.pt.2017.01.003
Vanderwaal, K. L., & Ezenwa, V. O. (2016). Heterogeneity in pathogen transmission: mechanisms and methodology. Functional Ecology, 30, 1606–1622. http://doi.org/10.1111/1365-2435.12645
Experimental design: The experimental design is very good and it is fantastic to be able to have such high resolution data. The authors give all the material for one to reproduce their results if one fancies. However, I feel that there are some missing bits and pieces in the analysis. Although the authors argue against not including those bits and pieces, I feel they would complete the story. One concerns including proximity or some kind of space sharing/use network as well as purely contact networks. I know that proximity and grooming are very often well-correlated but although the authors state several times that conditions (sunny and dry) are unfavorable for E. coli survival in the environment and that they did not find E.coli is tap water, they also state that E.coli can still survive up to 25 weeks. The fact that the monkeys are “forced” into proximity, a fact that the authors also highlight in the discussion, might indeed “expos[e] individuals more to environmentally deposited feces, [and] also increases the likelihood of social contact among animals that share the same space” lines 588-589. At least, I missed some more explicit discussion of this point.
A second one relates to the AMOVA. I understand the logic of conducting hierarchical modelling when one attempts to explain a pattern or phenomenon without assumptions or clear predictions. But here, 1/ there are clear predictions, and 2/ we know that factors influence each other, such that age and sex similarities and kinship influences grooming frequencies for instance which in turn could influence genetic similarity %. I am just wondering whether building a more integrative model with all factors at once would be possible? The separate testing of the effect of group membership, kinship, dyadic frequencies of interactions and individual characteristics leaves a feeling of incompleteness somehow. I am not sure but maybe a more classic generalized linear mixed model (with permutations) or Bayesian regression modelling may be able to sort out the variance linked to each factor at once?
Validity of the findings: Pending some methodological precisions and discussions, I think the findings will be robust and conclusions well linked to the questions. As said before, I also find the discussion in need of more straightforwardness. For instance, the authors spend 16 lines summarizing their results, lines 443-459, then another 6 lines shortly after, lines 464-470, repeating parts of those results before entering the actual discussion.
And of a broader picture viewing as well.
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: SOCIAL NETWORK COMMUNITY STRUCTURE AND THE CONTACT-MEDIATED SHARING OF COMMENSAL E. COLI AMONG CAPTIVE RHESUS MACAQUES (MACACA MULATTA)
Review round: 1
Reviewer: 2

Output:
Basic reporting: overall great! Although there is a lot of unnecessary pointing (e.g. see below). See general comments to the authors.
Experimental design: Excellent. The only issue is the fact that a single isolate was collected from an individual requiring cation in the interpretation of results. Some statistical tests are inappropriate for the kind of data. Again look at general comments to the author.
Validity of the findings: All findings are valid. However, caution is required in the interpretation on discordant findings. See general comments to the authors below.
Additional comments: The manuscript on social community structure and contact mediated sharing of E. coli in captive maca presents data indicating the value of social interactions as a proxy for inference of the transmission of infectious agents in group living organisms. The manuscript is worth publication in PEERJ after these issues have been addressed.
1.	Some statistical tests are inappropriate and needs redoing. Kolmogorov-Smirnov tests are compare the similarity in distributions and are not appropriate for comparing differences in percent similarity in E. coli between and within social clusters. A permutation / randomization test whereby percent E. coli similarity observed within DCG communities are compared with similarity obtained after shuffling individual across DCG and calculating the percent similarity between random pairs to generate the expected sharing assuming there is no influence of DCG on percent E. coli similarity among dyads.
2.	The authors make a claim that social processes are important in E. coli sharing BUT do not fully and comprehensively address the issues of non-concordant results between dyadic and group level social processes in the discussion or methods section of the manuscript. Because a single individual animal can have as many as 13 E. coli strains (see refs 1-3 below). Typing a single strain per individual can bring about anomalies in results observed in this paper such as similarity at the group level or some aggregated level such as behavioral DCGs but no signal is detectable at the dyadic level.  To obtain a detectable signal of dyadic interactions a single clone in a species where an individual may have several clones co-occurring will require repeated temporal sampling as the authors allude or intensive sampling more than four or more isolates to capture the full diversity within individuals and the latter is more powerful for E coli sharing and the former for tracking transmission. This should come out clearly in the discussion of discrepancy of results

3.	To make a solid claim on social processes in E. coli sharing, the authors need to run their data using hierarchical analysis of molecular variance (AMOVA) incorporating group and behavioral DCG social as to partial variance between group level effects which are environmental and those that are social (behavioral DCG)

4.	Specific comments. Please see attached copy with comments
Methods: Non parametric tests do not solve issues of interdependence but issues non-normality issues in data. You need tests that take into account such dependence.
References
1.	Ahmed S, Olsen JE, Herrero-Fresno A (2017) The genetic diversity of commensal Escherichia coli strains isolated from non-antimicrobial treated pigs varies according to age group. PLOS ONE 12(5): e0178623.https://doi.org/10.1371/journal.pone.0178623
2.	Anderson, M.A., Whitlock, J.E. and Harwood, V.J., (2006). Diversity and distribution of Escherichia coli genotypes and antibiotic resistance phenotypes in feces of humans, cattle, and horses. Applied and Environmental Microbiology, 72(11), pp.6914-6922.
3.	Bok, E., Mazurek, J., Pusz, P.A.W.E.Ł., Stosik, M.I.C.H.A.Ł. and Baldy-Chudzik, K., (2013). Age as a factor influencing diversity of commensal E. coli microflora in pigs. Pol J Microbiol, 62(2), pp.165-71.


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: SOCIAL NETWORK COMMUNITY STRUCTURE AND THE CONTACT-MEDIATED SHARING OF COMMENSAL E. COLI AMONG CAPTIVE RHESUS MACAQUES (MACACA MULATTA)
Review round: 1
Reviewer: 3

Output:
Basic reporting: No comment.
Experimental design: See general comments below.
Validity of the findings: See comments below.
Additional comments: This paper tests social predictors of E. coli strain sharing in three groups of rhesus macaques. It adds to the growing literature on the consequences of social interactions on microbial sharing/transmission, and is distinguished by a relatively large sample size and degree of environmental control. The main finding is that higher level social interactions, captured through “clusters” of socially interacting individuals, appear to better predict E. coli strain sharing than dyadic interactions. This result is likely to suggest new analysis approaches to researchers interested in this topic. I have a number of suggestions that I hope will be of use in any revision process.

Major:
1) The finding that DCG clusters are a better predictor of strain sharing than dyadic interactions is interesting, but it is unclear whether it arises as a consequence of biology versus technical artifact. With limited behavioral sampling (6 weeks per social group, mostly collected through scan sampling), dyadic estimates of grooming, huddling, and aggression rates may simply be less accurate than cluster/group-level membership. Can you show (e.g., using subsampling) that the amount of observational data collected produces asymptotically stable estimates for the three types of dyadic interactions you consider, compared to inference of cluster membership in the DCG approach? Are dyadic grooming, huddling, and aggression correlated? (If so, would combining these measures into some sort of sociality index produce a more stable measure of contact?)

2) K-S tests are used to compare E. coli similarity across communities. K-S tests are quite sensitive, since they test for differences in the cdf of two distributions, not differences in means—which I think is what you are most interested in knowing. If a non-parametric test is needed, why not use a Wilcoxon rank-sum test instead? Also, I could not tell if these tests were one-tailed (as suggested by the motivating hypothesis) or two-tailed.

3) Estimates of kinship are based on either matriline membership or a coarse binarization into close versus distant kin. How is a “matriline” defined? (how many generations back does it go?) Why binarize estimates of kinship? In the current scheme, distant cousins are treated as equivalent to full sibs; this approach seems less likely to detect effects of relatedness on strain-sharing, if they exist, than using pedigree or genetic marker-based point estimates.

4) Can you explain what DCG levels “mean” from a biological perspective? Do they tend to capture kin groups or sets of animals with close social bonds (c.f. Silk?)

Minor
-A single E. coli strain was isolated from each animal. Did you confirm that animals only carry a single E. coli strain? If they do carry multiple strains, can you explain how it might affect your results?
-line 27/28, 559, 563: “in the absence of phenomena like social buffering” What phenomenon are you referring to, and what’s its relevance to microbial sharing?
-line 132: “largely, these studies have defined…pairs of individuals from whom identical E. coli subtypes were isolated” Tung et al (and also other studies, e.g., Moeller et al in wild chimpanzees) actually use community composition (beta diversity) instead, or in addition to, sharing of individual OTUs. These studies have not analyzed E. coli isolates.
-The sample appears to contain adults only. Any ramifications of leaving out infants and juveniles as potential links in the social networks and/or routes of transmission?
-line 414: “dyads with an E. coli similarity >70%”—does that mean 70% of bands were shared, or 70% of 0/1 values for bands? What does it mean that this threshold is a “reliable indicator of pulsotype cluster membership and similarity?”
-Figure 2: I would find it helpful to see E. coli similarity levels for between group pairs to place the within group pair results in context


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: SOCIAL NETWORK COMMUNITY STRUCTURE AND THE CONTACT-MEDIATED SHARING OF COMMENSAL E. COLI AMONG CAPTIVE RHESUS MACAQUES (MACACA MULATTA)
Review round: 2
Reviewer: 1

Output:
Basic reporting: No further comment
Experimental design: No further comment
Validity of the findings: No further comment
Additional comments: Great study. No further 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: SOCIAL NETWORK COMMUNITY STRUCTURE AND THE CONTACT-MEDIATED SHARING OF COMMENSAL E. COLI AMONG CAPTIVE RHESUS MACAQUES (MACACA MULATTA)
Review round: 2
Reviewer: 2

Output:
Basic reporting: clear and unambiguous
Experimental design: Research questions are well defined
Validity of the findings: Statistical analysis is robust and the authors addressed the comments from previous revisions
Additional comments: None


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: EXPRESSION STATUS AND CLINICAL SIGNIFICANCE OF LNCRNA APPAT IN THE PROGRESSION OF ATHEROSCLEROSIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Meng et al have conducted a study of APPAT lncRNA and its use as a biomarker in circulating blood samples of angina and MI patients. The study seems to have an impressive depth and is overall well-conducted. However it suffers from lack of structure and stringency in reporting and could be much improved. While the English language itself is reasonable, I believe that the manuscript would benefit a lot from a work-through by a key-author, at each section asking if 1) the key points are clearly communicated, and 2) if superfluous information not necessary for key points could be removed. I have tried to give some examples below:
1.	One overall structure-suggestion. Shorten materiel and method (5 pages now)
It would be much better that each result section match med each figure.
2.	How to make the ox-LDL treated VSMCs of rabbit? What is the treatment? How? What is control for the treated cells?
3.	‘Randomly’ selected 2 up and 2 down regulated ? – I believe the word ‘randomly’ can be better described. It is important for the structure of the article.
4.	Figure 1B, there are no significant stars. How to calculate the significance? How many times was the experiment repeated? This should clearly be shown, also in caption
5.	Short description of results in figure captions.
6.	In figure 2, co-expression of APPAT and α-SMA is hard to see. There should be better indication of two kinds of scale bar.
7.	How to evaluate the expression level in fig 3?? There is no any description about it.
Experimental design: adressed in previous box
Validity of the findings: adressed in previous box (but seems valid)
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: EXPRESSION STATUS AND CLINICAL SIGNIFICANCE OF LNCRNA APPAT IN THE PROGRESSION OF ATHEROSCLEROSIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors have done a fine work in terms of professional English, providing background and describing the need/caveat the address.

Some points to address:
In the abstract, at lines 32-to-38, it states "To determine expression alteration of APPAT in coronary artery, we performed qPCR on samples of healthy and pathological coronary artery. Same test of APPAT level was performed on circulating blood samples from the normal and patients with angina pectoris or myocardial infarction, followed by calculation of prediction power of APPAT. Additionally, we predicted microRNA target of APPAT and the expression level of the target was primarily measured in human VSMCs cell line, coronary artery, and blood samples."
To me this doesn't read well. Something like "...artery. We also assessed circulating APPAT levels in blood samples from healthy individuals, and patients with angina pectoris (AP) or myocardial infarction (MI). Additionally, we predicted microRNA targets of APPAT, and show that the expression level of the targets was primarily measured in human VSMCs cell line, coronary artery, and blood samples. Lastly, we examined the predictive power of APPAT for the risk of AP or MI." would perhaps be better.
Experimental design: A power analysis of
- discovery experiment
- predictive power (ROC and AUC)
is lacking. Please add this.

Also include an assessment of the validity of the discovery given the many potential non-coding and coding RNAs that exist. In other words, is p = 0.05 a valid threshold? This threshold of discovery should be corrected for multiple testing.
Validity of the findings: Figure 1A:
I am missing the explanations for the abbreviations in the figure. What does CPC, PFAM, etc stand for?

Figure 1B: Perhaps I missed that in the manuscript, how do you explain the relative lower expression of APPAT in human cells as compared to rabbit cells after treatment with oxLDL?

Figure 2: Please include non-fluorescent HE, EvG and alpha-SMC stained histological slides of the same artery/plaques. This will aid in orientation with respect to the lumen and the remaining non-plaque area as compared to the IF-FISH images. This will also mean that Figure 3 can be dropped, unless it is the same sample. But together these Figures are not informative at the moment.

Replication  & Figure 4A:
- Please include data on the comparison between the two AUCs for APPAT and troponin.
- Is the AUC of APPAT *significantly* better then the one for troponin in predicting MI? In other words: what is the added value? Why not just use troponin?
- This is also lacking in lines 274-282: what is the statistical significance of these ROC/AUC analyses?
- Please, also include a power analysis of the ROC/AUC analysis.
- Furthermore, what is lacking is a replication of these results in a (larger) independent study. This is absolutely necessary and of great value to understand the relevance of APPAT as compared to for instance troponin as well as the validity of APPAT in predicting disease outcome.
- This has also implications for the discussion at lines 366-370 regarding the potential value of APPAT as a prognostic marker. I don't believe there can even be a discussion about this, as the validity of APPAT has not been tested in independent studies. This should be addressed in experiments and in the discussion.

The above also has implications for the conclusions made in lines 390-392. Things that would aid in support of the conclusions, and that would aid in assessing the validity of APPAT and miRNA-647:
- Please add in data on correlations (of APPAT and miRNA-647) in larger datasets with sub-phenotypes of atherosclerosis, for instance coronary artery calcification, and carotid IMT as these are strongly correlated to cardiovascular outcome.
- Are APPAT and the miRNA-647 correlated to other cardiovascular risk factors? One would assume there should be correlations with CAC, cIMT and risk factors, if APPAT and miRNA-647 are valid candidates diagnosis and prognosis.
- Are APPAT and miRNA-647 also present in carotid plaques? Or is it merely constraint to coronary arteries?
- Are APPAT and miRNA-647 also expressed in biosamples (i.e arteries) from GTEx Portal?

Figure 5: In figure 1B 'treated' is noted as 'oxLDL', for consistency that should also be the case for figure 5A.
Additional comments: In general nicely written, and well structured. What is really necessary though with this type of discovery efforts is to assess the validity of novel targets (verify) and replicate findings in independent and larger samples.


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: EXPRESSION STATUS AND CLINICAL SIGNIFICANCE OF LNCRNA APPAT IN THE PROGRESSION OF ATHEROSCLEROSIS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The authors propose the lncRNA APPAT as new player in the progression of atherosclerosis. The work is very interesting and potentially useful in future clinical studies. English could be improved in some parts of the manuscript.

The authors should share the raw data in public archives such as SRA or GEO before publication. It's possible to submit the data in a private format and then release them after publication. An accession number has to be provided in the manuscript, in the section regarding RNA-seq (methods section).

The section regarding miRNA target prediction is not completely clear. How did you select the miRNA candidates? Did you performed an intersection of target prediction algorithms? From the text this part is not clear. I suggest to write a paragraph about that in the methods.

Another point to be clarified is the p-value. Did you adjust the p-value according to FDR or other approaches? From the text it seems you used only the p-value in all the analyses.
Experimental design: The experimental design is correct and the use of NGS improves the quality of the results compared to the use of RT-PCR.

As suggested by the authors at the end of the paper, it is interesting to explore the mechanism of action of APPAT and also the potential interactions with miRNAs. I suggest to focus on extracellular vesicles extracted from serum and plasma for future experiments. In this way, you could be able to understand if APPAT is actively released in the bloodstream or not, and if the content of these vesicles is released inside target cells. Consequently, you could identify the "sponge" effect of APPAT in the target cell.
Validity of the findings: The findings support the hypothesis but future experiments are needed in order to validate the role of APPAT as non-invasive biomarker and its function and role in the progression of atherosclerosis.
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: EXPRESSION STATUS AND CLINICAL SIGNIFICANCE OF LNCRNA APPAT IN THE PROGRESSION OF ATHEROSCLEROSIS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors made good efforts to improve the quality of the article. There are no further questions from me. I hope that the authors will give more contributions in the field of atherosclerosis pathogenesis in the near future.
Experimental design: -
Validity of the findings: -
Additional comments: The authors made good efforts to improve the quality of the article. There are no further questions from me. I hope that the authors will give more contributions in the field of atherosclerosis pathogenesis in the near future.


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: FUSTR: A TOOL TO FIND GENE FAMILIES UNDER SELECTION IN TRANSCRIPTOMES
Review round: 1
Reviewer: 1

Output:
Basic reporting: In figure 2, a clearer description of the bar plot would be helpful. It is not very clear whether the x-axis represents the mean dN/dS of each gene family. If yes, the authors may also consider to add error bars.
Experimental design: 1. In the validation section, the authors may consider to include the performance comparison with other existing tools such as VESPA.
2. In the validation section, 2nd paragraph, the authors show that their method has very high sensitivity by identifying all 50 families that were simulated to undergo pervasive positive selection. The authors may consider to add genes that don’t undergo positive selection into their simulated data. It could be helpful to demonstrate specificity of their method.
Validity of the findings: No comment.
Additional comments: The authors developed a useful tool to detect the gene families and amino acid sites under positive selection based on transcriptomic data. This tool differs from other existing methods by allowing de novo transcriptome assemblies that are not predicted ORFs. The automated tool also simplifies the installation and analysis process. I think this paper will be of interest to the readership of 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: FUSTR: A TOOL TO FIND GENE FAMILIES UNDER SELECTION IN TRANSCRIPTOMES
Review round: 1
Reviewer: 2

Output:
Basic reporting: Besides the inconsistent "raw data", this report fits PeerJ's other "basic reporting" requirements. It must be stressed that while the dataset used for validation is very problematic (see "Problems with the validation dataset" in the "general comments"), the main issue here is that it is not adequate to test the performance of the pipeline reported here (see "Main issues" in the "general comments") and thus the pipeline should be tested using a different dataset.
Experimental design: Methods need to be described in further detail. In particular authors need to provide a more thorough documentation in the git repository (e.g. describe each subroutine and the intermediate files created by the pipeline) and a brief outline of the underlying procedures in the report for publication. Take advantage of the online-only nature of PeerJ and be as descriptive as possible. Remind that the better your documentation is and the easier for the user to understand how the pipeline is handling the data, the more users you'll have.

I celebrate that the authors have made available their method, so I was able to reproduce their analysis. For my testing I generate a non-redundant dataset of the sequences in Supplemental table 1 (530, removing 53 that are duplicates) and launched the FUSTr in a Linux machine with 4 processors. I labelled each sequence with its corresponding accession number, a short code for the species, and the "family classification" from the original publication (there were 9 "families" in the original publication).

>{gb ID}|{spe}|{family}

I then generated one fasta file per species (trying to emulate different transcriptomes for different "samples") and named the files as the short species codes. The 49 files contain between 192 and 1 sequences (there are 18 species for which contributing with only one sequence to the dataset). Trying to reproduce the potentially conflictive redundancy of annotation of the original publication and test the ability of FUSTr to recognize header patterns, I left four duplicated sequences labelled as both "ICKs" and "Huwentoxin-1_family" (i.e. they share the first two fields of the header). The input fasta files thus contain a total of 534 sequences, with four duplicates.

The pipeline is encoded in a Snakefile , for which I tracked back the calls and subroutines. The first subroutine is to duplicate the fasta files and stored them in "{sample}.clean" files, then headers are changed to comply with the conventions for the next steps. At this point, headers patterns are extracted from the files by the rule "newHeaders" and stored in  <headerPatterns.txt> file. Trinity's Transdecoder.LongOrfs is next called with a predefined "-m 30" option (minimal length for an ORF), which generates as much as six potential ORFs (the longest per frame), and the protein and nucleotide sequences are extracted with TransDecoder.Predict run on the <longest_orfs.pep> file, which predicts a single "best" ORF per input sequence.  An important control for validation at this point would be to check if the predicted protein sequences correspond indeed to the known translated sequences (a quick check at UniProt reveals that there are 133 transcripts in the dataset for which there is evidence at protein level). In my test, these steps removed 12 sequences from the analysis for no clear reasons as inspecting the Transdecoder intermediate files reveals that for all of them an ORF containing all of the known coding sequence was detected. The pipeline then assign a specific short ID for each best transcript model and writes two fasta files with all sequences as amino acids (pep) and nucleotides (cds).

An all-vs-all blastp is then run on the <all.pep.combined> file with a predefined -evalue 1E-5 and the output piped into SiLiX for clustering with a predefined minimum overlap of 0.9 (-r option). Per "family" fasta files are then generated by the node2families subroutine and large enough families (>14 sequences, it would be good if the authors provide a rationale for this choose) aligned with MAFFT, trimmed with trimAl and transformed into phylip (so codeml can be run). The protein alignments are also use to compute gene trees with FastTree. For a dataset as the one used for validation, all the previous steps are essentially completed in no time (less than a minute in my Linux  with four 2.93GHz cores).   I didn't have time to systematically check all retained ORFs, but in at least one "family" containing sequences named "lycotoxin" in the original publication (corresponding to IDs labelled as families 10 and 11 in the Supplemental Table 1) the predicted ORFs do not correspond to the known translated sequences.

For instance, the "best" ORF of FM863950 is

>Gene.187::FM863950_Lycsi_U1-lycotoxin_family::g.187::m.187 Gene.187::FM863950_Lycsi_U1-lycotoxin_family::g.187  ORF type:5prime_partial len:47 (-) FM863950_Lycsi_U1-lycotoxin_family:459-599(-)
TTTTTTTTTTTTTTTTTTTTTTTTTTTTTTTTTTTTTTTTGGAATCCTCAGAACTTTATCCAATTTAAAGAATGTTACAAACAAAAAAAATCAAAACAATTTTCTATGTCATTTTTGCTATCGTTTTACGAAATAATTTAA

Translated as

>Gene.187::FM863950_Lycsi_U1-lycotoxin_family::g.187::m.187 Gene.187::FM863950_Lycsi_U1-lycotoxin_family::g.187  ORF type:5prime_partial len:47 (-) FM863950_Lycsi_U1-lycotoxin_family:459-599(-)
FFFFFFFFFFFFFWNPQNFIQFKECYKQKKSKQFSMSFLLSFYEII*

But the original sequence is

>FM863950.1 Lycosa singoriensis mRNA for toxin-like structure LSTX-A23 precursor (LSTX-A23 gene)
GACAGAACTTCGGTTTAGTTCCCCAGGAAATTTTGACTAAGTGACATCTTGAGGTTTCCTCCCAGCCAATCATGATGAAGGTTCTAGTGGTCGTTGCTCTTTTGGTTACTCTTATCAGTTACTCTTCAAGTGAAGGGATTGACGATCTTGAAGCTGACGAACTGTTGTCTTTAATGGCCAACGAGCAAACCAGGAAAGAATGCATTCCCAAACACCACGAATGTACGAGCAATAAGCACGGCTGCTGTAGGGGTAACTTTTTCAAATACAAATGCCAGTGTACAACAGTTGTTACCCAGGACGGAGAACAGACCGAAAGATGCTTCTGTGGAACTCCCCCTCACCACAAGGCGGCCGAATTGGTGGTTGGCTTCGGGAGGAAGATTTTCGGATAAAAGAACAGCTTTATCGGAATATGTGAAGACACGTTATTTGACGTAAATGAACCTCTGTAGAGTTTAAATTATTTCGTAAAACGATAGCAAAAATGACATAGAAAATTGTTTTGATTTTTTTTGTTTGTAACATTCTTTAAATTGGATAAAGTTCTGAGGATTCCAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAAA

Translated as
>CAS03548.1 toxin-like structure LSTX-A23 precursor [Lycosa singoriensis]
MMKVLVVVALLVTLISYSSSEGIDDLEADELLSLMANEQTRKECIPKHHECTSNKHGCCRGNFFKYKCQCTTVVTQDGEQTERCFCGTPPHHKAAELVVGFGRKIFG

Thus, the identification of the coding regions by Transdecoder on this dataset is not optimal (notice that the predicted ORF contains the polyA region of the original sequence). This means that the gene tree and the selection tests were not performed with the coding sequences, and the results are therefore bogus. The authors must debug this problem and document their findings (e.g. is there a way to optimize the selection of the best ORF?).

Moving on, the last and most computationally expensive step performs codeml analysis (using a biopython-inspired wrapper) under 7 different models of dN/dS distributions and testing for the most likely model of selection (achieved by comparing the log likelihoods). In my test, 9 families were automatically processed in just under 20 hours. If I understand correctly the summary file (a three-column file not described in the report, nor in the git, with four model comparisons per family), in my test three families are under "positive selection" (i.e. p<=1e-2 for models allowing dN/dS>1 vs models with fixed or variable dN/dS<=1), two of which correspond to kunitz toxins, in-line with what is reported by the authors, but also including the family containing the bogus ORFs of lycotoxins. Although the authors have not documented how  they obtained the plot in Figure 2 (alas, it would be better if they do), I parsed the *mcl files and found 15 and 5 sites with dn/ds>1 in each of the kunitz families (I suppose corresponding to "kunitz 1" and "kunitz 2", respectively, in the figure).
Validity of the findings: The "validation" and simulated datasets are not adequate to test the performance of FUSTr. The amount of data in both cases is unrealistically small for a typical transcriptome study, let alone for a tool intended to analyze several transcriptomes at once.
Additional comments: Suggestions for improvement
- Perform the "validation" on a relevant dataset, this should include potentially conflicting sequences (e.g. multiple isoforms derived from a single gene) and identifiers. One alternative would be to generate Trinity/cufflinks transcriptomes from publicly available SRAs known to be rich on multi-gene families
- Document all the steps performed by the pipeline (the more detailed the better)
- Include the raw fasta files for the validation datasets in the git repository
- If authors choose to maintain the current "validation" dataset as an additional proof of the performance, the dataset must be corrected for the several inconsistencies detailed below and the inconsistencies in the original dataset described
- Provide the results of the simulated dataset in graphical form

Main issues
1. "Validation" dataset is not adequate for testing the features of the pipeline
The dataset used is a manually curated set of full precursor sequences originally analyzed in PLoS Genetics 11:e1005596 and contains less than 600 sequences. This is an unrealistic size for transcriptome based studies, where thousands of transcripts would be predicted from a single experiment.

2. Insufficient description of the methods
The pipeline is not properly documented, with several steps not even described (e.g. the construction of new headers and the processing of the codeml outputs), non described third-party options  (e.g. blastp evalue and SiLiX minimum overlap). See extensive comments in the "Experimental Design" section.

Problems with the "validation" dataset
I will comment on the several inconsistencies of what I consider very problematic "raw data" (in this case the dataset used for the validation part), but it should be kept in mind that, as described above, the dataset used for validation is not adequate for testing the purposed use of FUSTr.

- The number of sequences analyzed here is reported to be 624 in the text (marks 100-101), but numbers in Table 1 add up to only 618, whereas there are only 583 accession numbers in the supplementary file. I would have expected the authors to identify this not minor inconsistency before, but I understand it may be related to the not well structured presentation of the original publication (PLoS Genetics 11:e1005596, 2015). For the sake of this review, I have downloaded the relevant files from https://doi.org/10.1371/journal.pgen.1005596.s005 (including the reportedly accession numbers reportedly used) and https://doi.org/10.1371/journal.pgen.1005596.s006 (reportedly including the codon based alignments used for testing selection). Whereas the total number of analyzed sequences is not reported in the original publication, there are nine named "spider toxin families" in the supplementary files (alas somehow ten are plotted in figure 1of that publication), including 708 sequences in the alignments (four sequences appear in two different alignment files) and only 686 in the accession number tables. I regret these inconsistencies were left unattended in the original paper, but here the authors have the chance to correct the public record. I could map 567 identifiers shared between this report and the original publication, the remaining 16 identifiers correspond to the "FUSTr family 5" (omega hexatoxin in Supplemental Figure 4) for which the IDs in the original publication were not-standard.

- The number of "highly curated spider venom toxin protein families" analyzed is said to be seven in the text (mark 100), all of which are said to be correctly recovered by FUSTr (mark 103). The eight bars in Figure 2 reflect the fact that "kunitz toxins" were split into two groups by SiLiX's step of FUSTr). Further inspection of the Supplemental Table 1, reveals that the 583 sequences are actually classified into 23 similarity clusters by the pipeline, nine of which contain 10 or more sequences and including five cases in which several FUSTr-derived clusters mapping to a single "family" as (ill-) defined in the original publication.

- The dataset analyzed also has problems regarding the assumption of phylogenetic independence (identical sequences, unknown biological sources, erratic phylogenetic breadth, etc).


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

Input:
Title: FUSTR: A TOOL TO FIND GENE FAMILIES UNDER SELECTION IN TRANSCRIPTOMES
Review round: 1
Reviewer: 3

Output:
Basic reporting: no comment
Experimental design: It is not very clear to me how the simulated data generated in validation section (Starting from line 106). Also, in the implementation part, it seems that FUSTr performs many processing steps for input data. However, one question I have is that is this a data-driven model? For example, does the output purely come from the clustering results? Is FUSTr aimed to identify how many gene families exist in the input sequence?
Validity of the findings: no comment
Additional comments: No additional comments


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

Input:
Title: FUSTR: A TOOL TO FIND GENE FAMILIES UNDER SELECTION IN TRANSCRIPTOMES
Review round: 2
Reviewer: 1

Output:
Basic reporting: I agree that the new real life dataset  provides an "ideal case use for FUSTr",  however is not really a benchmark. In the original publication, more than 2000 homologous loci were identified in six specimens from two species. In that publication, less than 70 loci were identified as being under selection for color-changing or colonization phenotypes. I think it would be interesting if the authors double check if the families identified as under selection by FUSTr are the same. It would be also interesting to see if other multi gene families are also under selection.
Experimental design: Although I'm happy with authors responses to the previous round of revisions, in particular the with the new validation dataset, and that I celebrate the almost complete re-engineering of the pipeline, which now relies on Docker as container and snakemake for workflow management, I would encourage the authors to further document the potential problems their intended users could face. For instance, Docker requires root privileges for running commands or to create a group of users that also needs root privileges, which many users might not have. Also is not clear for me if the setup_docker should be run every single FUSTr run (i.e. with different data folders). This time I was not able to reproduce authors' results, due to conflicts with my system configuration. Yet, I can follow the rationale in the Dockerfile, Snakefile and FUSTr wrapper and I do not think there should be any problem to reproduce the analysis step by step.

In my test, the docker daemon fails while trying to "apt-get install -y wget git build-essential cmake unzip curl" (all of which are part of the any linux distribution) and exits with a non-zero code. When I tried tweaking the FUSTr wrapper to run the pipeline, I faced an "snakemake: error: unrecognized arguments: --use-conda" which leas to another non-zero exit status 2.

$ conda -V
conda 4.3.30
$ snakemake -v
3.13.3

My suggestion at this point is that the authors document all the programs needed to run the pipeline and offer an alternative customizable wrapper that the user can modify to point to the local installation of the programs (do the user really needs to re-install everything every time?).
Validity of the findings: nothing to add
Additional comments: nothing to add


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: DISTRIBUTIONAL DYNAMICS OF A VULNERABLE SPECIES IN RESPONSE TO PAST AND FUTURE CLIMATE CHANGE: A WINDOW FOR CONSERVATION PROSPECTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Initially I was a bit concerned about the use of English but this was quickly dispelled. The article is generally well written however I request that the earlier sections, up-and-till  the Results, be re-checked for use of English, particularly sentence construction.
Experimental design: The reader may not be familiar with Pseudolarix amabilis hence it is important to provide a bit more useful background but relevant information. State that it is a tree, occurs family Pinaceae, and provide a few additional plant traits such as it has cones with winged seeds, pollination by wind, longevity, etc.

Provide its full IUCN red list status.

Sentence in Lines 145-147. Please reword ending as approach is not clearly articulated.

Figure 3 (A). The arrow direction should be reversed as it currently shows migration from expansion areas to  contraction/no change areas. (B) is correct.

"Figure 4. Main limiting climatic factors for the distribution ..” add word “climatic”
Validity of the findings: Lines 408 to 411. I am uncomfortable with this statement. The model shows sensitivity to climate change and not necessarily the species, given the limitations discussed.
Additional comments: There is no mention of the likelihood that some populations occurring during the LIG and LGM periods could have gone extinct and therefore their locations and influence on Maxent model could not be included  (and therefore the models may be slightly more conservative, failing to include extinct populations).


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: DISTRIBUTIONAL DYNAMICS OF A VULNERABLE SPECIES IN RESPONSE TO PAST AND FUTURE CLIMATE CHANGE: A WINDOW FOR CONSERVATION PROSPECTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall the paper seems fairly sound, and should eventually be published I believe. It uses well established methods to predict past, present and future suitable climate areas for one  particular plant species It has various issues that should be addressed before it is published, as detailed below.

Literature references and sufficient field background/context are provided in most places, with some exceptions noted below.

The structure of the paper is ok, but some revision of Discussion is required (Discussion too long, first paragraph should focus on your results, contains some material that should be in Results, see below for details).

I would say the paper just represents an appropriate 'unit of publication'. SDM studies like this are becoming so easy to do, with the general availability of data on species presence and climatic variables. It would seem relatively easy to do the same study done here for another species, and another, and another and so on. I wonder whether each one would really deserve its own publication? I think studies that focus on several species at once are already becoming the norm (eg. Yates et al and Hamer et al below). Perhaps these could be referenced as examples of what such studies could try to encompass in future? Nonetheless, I think this study just meets the requirements for an appropriate 'unit of publication'.

Yates, C.J., McNeill, A., Elith, J., Midgley, G.F., 2010. Assessing the impacts of climate change and land transformation on Banksia in the South West Australian Floristic Region. Diversity and Distributions 16, 187–201. https://doi.org/10.1111/j.1472-4642.2009.00623.x

Hamer, J.J., Veneklaas, E.J., Poot, P., Mokany, K., Renton, M., 2015. Shallow environmental gradients put inland species at risk: Insights and implications from predicting future distributions of Eucalyptus species in South Western Australia. Austral Ecology 40, 923–932. https://doi.org/10.1111/aec.12274

The English language should be improved to ensure that an international audience can clearly understand your text. In many places the choice of words, or tense or expression is a real barrier to understanding the science.

For example, in the abstract:

“To avoid potential biodiversity loss, biological conservation is
significant,” should be “To avoid potential biodiversity loss, biological conservation is
important,”

“While future modelling discovers a significant migration north of the potential climatically suitable areas of this species relative to current ones.” is not a sentence.

Lines 65-66

121 ‘literatures’ is not correct

The tense used seems incorrect at times. For example, the present tense is used in Materials and Methods for things that were clearly done in the past. This has real consequences for understanding the meaning of the text. These is sometimes an inappropriate mix of tenses.

Further examples are provided in the general comments below.
Experimental design: The study seems to follow a very established standard procedure for MaxEnt species distribution modelling and uses well-established software and methods. There is little that is original in the approach, beyond applying the established methods to a new species, but the flip-side of that is that there is little to criticize since the methods are so well established. The authors do also acknowledge some of the limitations of this kind of approach in the Discussion, which is good to see, but this should be better referenced, including references to more mechanistic approaches that are trying to overcome some of these limitations (see below for more details).
Validity of the findings: There is very little detail given on the climate projections used, and yet obviously all the results depend intimately on the climate assumptions used. The climate layers for the past climates and especially the one for the future climate must be very suspect, in terms of accuracy. This is somewhat acknowledged in the Discussion, but I would like to see some more details in the Methods as well, on how these climate layers are generated and how confident we can be in them (see details below).
Additional comments: The use of the word ‘window’ in the title seems strange to me. What does it mean??

Abstract, line27 “The response mechanism revealed,” It is unclear what the response mechanism is as it has not been mentioned previously in the abstract.

98-99 not clear to me how reconstructing range dynamics can reveal actual mechanisms… can you explain or provide a reference?

110 you cannot say that MaxEnt always has excellent predictive performance. It will always depend on the data, whatever the modelling approach used.

98-112 Overall this paragraph is not convincing. Maybe this is because of the references to response mechanisms. MaxEnt and most climate envelope methods are NOT mechanistic… they are purely statistical/descriptive. 101-112 is a reasonable summary of this kind of modelling, but its justification at the start is not convincing to me.

115 Following from the previous paragraph, the overall aim is not clear. ‘revealing the response’ – ‘revealing’ sounds like you are finding the actual response, but rather you are ‘predicting’ or estimating or ‘modelling or foracsting/hindcasting’ I think.  “provide a theoretical foundation for future conservation strategies” – this sounds too vage to me to be a real scientific aim, or at least it needs more detail on how the distribution predictions will help future conservation strategies

124: I think some more information is needed on these climate layers, especially the past and future ones. How are they generated? How confident are we in them? For the future one, I think there are many different models and methods and emission scenarios that can be used to generate such layers… which were used in this case? How do your results depend on these choices and would conclusions be different if different climate models and emission scenarios were assumed?

127 – model overfitting is model overfitting… I would say that it cannot be exacerbated in certain conditions. However, the impacts of overfitting will be seen when the data is applied to new conditions.

129 – you don’t remove all environmental predictors with high pairwise correlation I think… you remove all except one??

131 – what is “the physiological role of P. amabilis”?? I think the word choice is wrong.

131-132: what is a low percentage contribution? How low is low?

135: “too many correlated parameters” – no, it is not the parameters that are correlated, it is the explanatory variables, right?

144: These two sentences seem unconnected, so I do not understand why ‘however’ is used for contrast here. How is the first sentence related to the rest of the paragraph?

149: why is it a bias FILE? Is file the right word choice?

151: what layers? ‘layers’ hasn’t been mentioned in this paragraph, or the one before. Is this something to do with the bias ‘file’?

153: the use of present tense here makes it sound like the authors are claiming this is the only way to assess predictive performance, but it is definitely NOT. I think they mean that this is how they chose to assess it??

159: and here past tense its used (was). The mix of past and present tense is very confusing, as it strongly impacts the meaning, as per the example above.

165: “by excluding the 10% most extreme data points in the modelling” – I don’t think you are excluding data points? Rather you are excluding predictions???? In either case, 10% most extreme in what sense/direction???

168: so why include the 10% TP at all?

169: ‘survey’? I don’t think you are actually surveying anything?

172: again the use of ‘file’ is confusing. I think you mean you calculate the vector? The fact that you store this information in a file is incidental surely.

176: “finally, we evaluate the potential migration from one period to the next” – too vague. How did you actually do this based on the centroids explained above??

181: “We focus on the limiting factors affecting the contraction and expansion of climate suitability.” – again, this is vague. What do you mean by this?

186: No, perfect would be AUC=1 ??

188: well predicted rather than well described I think

189: Do these values mean anything? Are they low or high or good or bad?

217: acronyms not useful – explain in full

Discussion.

222-233The content of this paragraph does not refer to results at all. It reads more like general background. It should be in the Introduction, or come later in the Discussion when discussing caveats on the study. The first paragraph of the Discussion should focus on the most interesting results of your study!!

236-241: This is not Discussion, this is Results! The Results section is for presenting results, like this. The Discussion section is for saying why they are interesting, important, relevant, applicable, expected/unexpected, etc etc

255: what’s TS and AP? Overuse of acronyms, especially for Discussion which may often be read in isolation.

258: “the regional heterogeneity of climate baseline and the different amplitude of the variable’s variation” I don’t understand – should be clarified.

Overall the Discussion has many interesting points, but it is much too long and unfocussed. I think it should be substantially rewritten to much better focus on the most important points of YOUR study. For example, 283-290 has no reference to your results at all.  In fact 246-290 has only very occasional and brief reference to your results.

The final paragraph on limitations could be much better referenced. The limitations of MaxEnt-style correlative SDMs have been well discussed by many others (eg Fordham below, but many others as well). People are starting to address some limitation using more mechanistic modelling approaches and these should be acknowledged. The CSIRO CLIMEX model is one example, as are the papers below, and there are many others. Some of this work should be acknowledged.

Fordham, D.A., Resit Akçakaya, H., Araújo, M.B., Elith, J., Keith, D.A., Pearson, R., Auld, T.D., Mellin, C., Morgan, J.W., Regan, T.J., Tozer, M., Watts, M.J., White, M., Wintle, B.A., Yates, C., Brook, B.W., 2012. Plant extinction risk under climate change: are forecast range shifts alone a good indicator of species vulnerability to global warming? Glob Change Biol 18, 1357–1371. https://doi.org/10.1111/j.1365-2486.2011.02614.x

Renton, M., Shackelford, N., Standish, R.J., 2012. Habitat restoration will help some functional plant types persist under climate change in fragmented landscapes. Global Change Biology 18, 2057–2070. https://doi.org/10.1111/j.1365-2486.2012.02677.x

Tomlinson, S., Webber, B.L., Bradshaw, S.D., Dixon, K.W., Renton, M., n.d. Incorporating biophysical ecology into high-resolution restoration targets: insect pollinator habitat suitability models. Restor Ecol n/a-n/a. https://doi.org/10.1111/rec.12561


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: DISTRIBUTIONAL DYNAMICS OF A VULNERABLE SPECIES IN RESPONSE TO PAST AND FUTURE CLIMATE CHANGE: A WINDOW FOR CONSERVATION PROSPECTS
Review round: 1
Reviewer: 3

Output:
Basic reporting: This paper presents a modelling-based study of the historic, present and future distribution of Pseudolarix amabilis, a conifer with a restricted distribution in eastern China. My personal field of expertise is ecology, not modelling, and thus I have appraised the paper on the bases of its ecological relevance and interpretation rather than the technical strength of its modelling approach.

Firstly, the flow and content of manuscript could be improved to help the reader along the journey of the study. At present parts are not concise, particularly the introduction – at four pages long it is a rather rambling background to the study, and several sections could perhaps be removed as they are not intrinsically relevant (LL31-46) or should be consigned to the methods (L101-112). Similarly, the discussion at 11 pages is far too long and reads somewhat like an unfocussed essay. The first paragraph of the discussion makes no reference to the results of the study, which again makes interpretation difficult. Additionally, some elements of the discussion (e.g. L236-241) belong in the results. I was not left with a clear understanding of the study outcomes, how these related to other international literature, or whether the study had achieved its aims of informing future conservation. In fact, the last paragraph seems to suggest that the available data are not sufficient to achieve this aim and that future studies using ENMs might be sufficient. As the reader I need to be led through the study of the study and left with no uncertainty about what was undertaken and why, and the significance of the findings need to be clearly articulated. I am afraid this was not the case – from the summary paragraph (L408-414) I took the message that P. amabilis responds to climatic change exactly as one would expect, and I am afraid I disagree with the statement that “investigating the response mechanism of P. amabilis to past climate change and predicting future climate suitability results in an effective conservation strategy”. This study doesn’t examine the response mechanism of P. amabilis (rather it examines a modelled response underlain by many, many assumptions), and effective conservation requires implementation of actions rather than simply predicting a future scenario.

Fig S1 – very difficult to distinguish between symbols for historical distribution given colour and overlap.

Table S1 – Bio variables should be arranged numerically to match the caption

I think overall, the paper fails this section in its current form.
Experimental design: The paper presents something of a case for conservation, although I feel this basis for the study is rather weak – particularly as the authors don’t really background how threatened the species actually is. The IUCN Red List assessment for P. amabilis notes “this species is very rare in the wild and occurs in a few remnants of primary forest on isolated mountains. Most locations are not within protected areas and loss of habitat is still continuing in this densely populated part of China.” Area of occurrence is estimated at <500 km2, and threatening processes continue unabated. With this in mind, it seems the species requires more pressing conservation initiatives than future modelling – predictions would suggest it may be extinct in the wild long before the 2080 scenario modelled.

Following on from this point, why was the “future moment (2080, HadCM3 A1B)” chosen? There is no justification provided in the text. Is this widely considered to represent the future climate of the region? Does only one modelled snapshot of the future provide an adequate assessment of future conditions and the variability in future climate predictions?

My main issue with the paper is this: the authors provide little discussion of the ecology of the species, which is in my opinion crucial information for the reader in interpreting their results. For example, in the introduction the only non-distributional information about the species (which is only introduced in line 86) is that it belongs to a monotypic genus. We only find out that P. amabilis is a tree as a side note on line 245 in the discussion, and nowhere is it stated that the species is a long-lived conifer restricted to acidic soils between 180-1000 metres altitude (all information provided in the IUCN Red List assessment that is critical to interpreting species distribution). How long-lived is the species? Many conifers are long-lived and take many years to reach reproductive maturity; is 80 years sufficiently far in the future to account for multiple reproductively successful generations? 80 years seems like a very near snap-shot of the future compared with the past in a physiologically adaptive sense (particularly for long-lived individuals): the species had ca. 120,000 years to adapt to changing climate between the LIG and LGM, 21,000 years to adapt between the LGM and present, but only 80 years between the present and the future scenario. I imagine if they are not logged, many individuals alive today will still be alive in 80 years which would imply no change in distribution from climatic factors; rather perhaps a change in the suitability of climate for seedling germination to occur if we work off the assumption that seeds possess a narrow thermal/hydrothermal envelope and exhibit thermal suppression at temperaures 1-2 degrees greater than the present (unlikely based on the global literature). Additionally, there is also no information provided on the dispersal strategy of the species (though there is significant conjecture about past distribution, dispersal, and habitat occupancy).

The authors acknowledge that they do not include soils data in their analyses due to a lack of available data (and note that this omission may limit the efficacy of the model). This is unfortunate given the species has known soil affinities, but is perhaps understandable if such current or historical data is not available. However, the authors also make no mention of altitude or elevation in their manuscript. This to me seems like a terminal oversight given the literature notes the species to be elevational restricted. If the chosen future climate scenario is one in which conditions are warmer than present (this is not clear), then surely an analysis of geographic area incorporating elevational data is required to assess the altitudinal shift in distribution – and this would surely make the situation of the species far more dire.
Validity of the findings: See many of my comments in section 2.
Additional comments: No general comments.


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

Input:
Title: DISTRIBUTIONAL DYNAMICS OF A VULNERABLE SPECIES IN RESPONSE TO PAST AND FUTURE CLIMATE CHANGE: A WINDOW FOR CONSERVATION PROSPECTS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors appear to have exhaustively addressed the comments of the reviewers in their response document, and provided significant background to these responses in their rebuttal. The quality of English throughout the manuscript has been improved somewhat.  The introduction is to me still rather long, but this is not a huge concern.

The aims and hypotheses are much clearer, and the significance and outcomes of the study are presented with much greater clarity. The addition of ecological information on the species is appreciated and adds to the manuscript, although I feel “branchlets are dimorphic: long branchlets (leading shoots) with helically borne leaves and short branchlets (brachioblasts) with fascicularly arranged leaves.” (L84-86) Is probably unnecessary as morphology is not relevant to the study.
Experimental design: The methods appear well-structured and are presented with a high level of detail. With the additions made after the initial review, I feel these are now satisfactory.
Validity of the findings: I still feel to some extent that this study lacks ecological significance; that is, the data presented are heavily constrained by the absence of soil and altitudinal data given the relevance of these factors on the species distribution. As far as I can see, there is also little attention paid to the highly fragmented nature of remaining natural habitat (very little of which remains in the study region). The authors have acknowledged some of this, and explained why they are not included in the rebuttal, and while I accept this explanation I do wonder how meaningful the conclusions that have been drawn are in their absence. The identification of (for example) 100 km2 of climatically suitable habitat is not particularly useful if half of this is unsuitable soil type, three quarters of the suitable soil type is developed land, and only a fraction of the remaining area is altitudinally suitable. All of these factors are critical for seed germination and seedling establishment, which the authors have noted is the primary life cycle stage they are modelling. As a side note, proper examination and modelling of these factors would require an understanding of seed dormancy, seed ecology, and the thermal niche required for germination to occur, as well as looking at shifts in seasonality which may impact upon moisture availability during critical life cycle stages.

My concern, essentially, is that the authors may be significantly overestimating the future distributional envelope of this species. However, I understand their argument that some of this critical information is not available. I have deliberated on this for some time and cannot decide how to appraise this; I will defer to the opinion of the editor on whether this issue is significant enough to hinder publication.
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: PHYLOGENETIC RELATIONSHIPS AND GENETIC DIVERSITY OF THE POLYPEDATES LEUCOMYSTAX COMPLEX IN THAILAND
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Buddhachat and Suwannapoom conduct a phylogeography of frogs belonging to the Polypedatus leucomystax complex occurring in Thailand. There is a basis for an interesting paper here, but in current form I find it unfocussed. I find it difficult from the present paper to get a good idea about this complex, not only in general, but also the situation in Thailand. Particularly relevant for this study is that it is not clear how many species are supposed to occur in Thailand and if they are all included. The aim of the paper is not clear. Obviously the presence of cryptic species in the complex and potential co-occurrence of such species is a big part of it. However, the paper suffers from equating mtDNA clades with species. I suggest to tone this way down and merely suggest that mtDNA clades might suggest additional species and sympatry of species. You have much more work to do before you could talk about species (morphological, bioacoustics, nuDNA analyses) and this should be acknowledged in the paper. The mtDNA data help raise testable hypotheses, but they don’t solve this complex of species. Furthermore discussion on the difficulties of mtDNA-based species hypotheses is missing. What about mtDNA ghost lineages? What about mtDNA introgression? This paper is quite light on references and this can be explained by lack of discussion of such evolutionary processes. Finally I think the biogeographical aspect of this paper should be fleshed out. Obviously in the set-up of the paper you want to explain why there is such a richness of (cryptic) species in the region and furthermore the data provide insights on biogeography. The authors seem to not have realized that the Istmus of Kra is an important biogeographical boundary and there is much digression in the discussion that can be ditched. These frogs once again validate this boundary and that is something to discuss in a wider context. I think the presentation of the mtDNA data can be better. The paper is quite well written but I do note some obvious issues. I give more details below.

The set-up of this work in the introduction is not optimal. This concerns the first and lines 81 – 83 from the last paragraph. These need to be combined as currently the flow of the introduction is cut up. I suggest first para the greater context of this study, second para the system (so as it is now) and third para the aims of the study (so lines 83-87). Regarding the set-up, I think it makes sense to start about SE Asia as a hotspot for amphibians. However, lines 50-53 are just a list of taxa with references and the link with the present work is not clear. This could be fleshed out however. I feel that this work is mostly about cryptic species and that is a good angle. It also makes sense to give some more background on the historical biogeography of the region to explain why there are so many species and to use new phylogenies such as created here to inform on historical biogeography.

About the study system: it is very difficult for me as a reader without knowledge on this system to grasp this. Are all the species you listed members of this complex and are all other known species of Polypedates not members of this complex. If so how was this determined? How are the relevant species distributed (perhaps provide a map with ranges and type localities?).

Line 45: remove substantial as hotspot already suggests biodiversity is substantial

Line 79: a complex is not a cryptic species, but a complex may contain cryptic species.

Line 49: remove “in the current period” or change to “observed today”

Line 54: Change “The clarification of ambiguous species” to “Accurate species delimitation”

Line 91: It is mentioned in the introduction that five (described) species of the complex are found in Thailand. But why are not all species included in this study? And which species are included? It is not clear to me how you chose the sampling that you did. Is it perhaps the case that some described species cannot be distinguished based on mtDNA?

Line 129: It seems like you directly provide a result here. In the Methods you should say you used Barrier 2.2 and why, but not what the outcome was, that should be in the Results.

Line 130-131: THE minimum spanning network >>> A minimum spanning network

Line 143: to assume should be assuming?

Line 144: Multiple should be multimodal?

Lines 161-164: It is not clear how you go from clades to species names. Do you base that on included sequences that were ascribed to a species? You need to be explicit. Of course you run the risk now of equating mtDNA with species while that is a dangerous interpretation without other data such as morphology and nuDNA. So you need to bring these names in carefully. It needs to be explained where the use of Polypedates sp. comes from. Does that mean this clade cannot be ascribed to a particular species while the others can? And if so, is that because you simply did not include relevant species or is it likely to be something new? It is not clear. I think it is not a good idea to talk in the Results about species rather than clades, for example describing the distribution of species based on mtDNA clades. If you want to interpret clades as species you would do that in the Discussion, but of course you need to be very, very careful there because mtDNA alone is not a good basis for species delineation.

Line 161: “Bayesian analysis model with MrModeltest” this phrasing makes no sense. You also did a Maximum Likelihood analyses. Don’t repeat methods.

Line 162: could consists >>> either just say consists or something that you recognize four clades.

Line 165: I guess you mean inference?

Line 174: incomplete sentence

Line 174-175: this is interpretation and does not belong in Results.

Line 176-177: This sentence is gibberish.

Line 181-186: there seems to be circularity here. You have allocated clades and hence haplotypes to species and now you say haplotypes belong to species. And what do you mean with unique haplotypes?

Line 202-203: Remove “one of the most notoriously challenging” as I can think of a million other difficult groups.

Line 204: You do not SOLVE anything, you get a little bit closer to the solution or at least to a hypothesis.

Line 205-208: These sentences should not be here. They just show that you should have used another marker than COI. But that is the marker you have so that is what you have to stick with. These studies may provide some insight into the system (I am not going to read them) and might be worth to integrate into the introduction of the study system, but there is no point of mentioning this here.

Lines 208-214: What you do here is just not right. You cannot just assume that these four clades are species and that these species occur sympatrically. You could only do that if you had independent data to delineate species, such as morphology or nuDNA. What about mtDNA introgression or simply the occurrence of distinct mtDNA clades in a single species? I am familiar with European newts and all these issues occur here. Related to this and hinted to in Line 221-222, apparently morphology could give some insights and you have looked at morphology but only as an aside? I noticed you have collected whole individuals so either you would do a morphological analyses of all these samples to see if you could come up with a morphological based species delineation to compare your mtDNA dataset to, or you do not make larger claims than that the mtDNA supports and can support.

Line 223-225 & 228-229: again, how do you link these names to these clades, it is not clear. Is it based on and ID given to a sequence taken from GenBank? If so you need to be clear on this (and what if the ID on GenBank is wrong?).

Lines 227-228: This is a strange sentence, it seems to suggest that somebody already looked at the exact same frogs and found the same pattern, but that is not the case. You mention another taxon where this pattern was found. Be more clear, so say it was stated in another taxon. However, there is much more to it than just a single other taxon, this is a known biogeographical boundary (also applies to  lines 233-238). Isn’t this the official boundary of the Sunda region? This needs to be worked out because it is this kind of historical biogeographical inferences that are juicy results. Lines 243-247 seem to suggest that nobody before knew that this was a biogeographical barrier…

Lines 239-243: I don’t see what is the point of this section? So they could be moved by people (but I guess islands would also have been connected to the mainland during glacial times?) but how does that relate to the current work? You find a clear biogeographical boundary despite any artificial movement.

Lines 248-265: I don’t see the point of this section. There are two biogeographical regions and these frogs seem to show a divide as well, that is the bottom line (and for all the sympatric lineages you have no idea if they even are species and if so what separates them).

Lines 266-284: again you talk about a particular species without justification. Why would you need to invoke human-mediated translocation to explain homogeneity? Why not a recent population expansion from a small source population?

In the conclusion you talk about putative species and clades and this is the proper route to take.

Fig. 1 This legend is a mess.

It makes MUCH more sense to show clades instead of haplotypes in Fig. 2. This way the clades in Fig. 1 can be directly linked to the map and that is way more insightful. The present use of colours in Fig. 2 is poor, I cannot distinguish different shades of yellow etc. In Fig. 3 colouring the haplotype network according to populations is pretty pointless and actually very confusing. This haplotype network is better presented as part of Fig. 1. Just use the colours of clades for the haplotypes belonging to clades.


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: PHYLOGENETIC RELATIONSHIPS AND GENETIC DIVERSITY OF THE POLYPEDATES LEUCOMYSTAX COMPLEX IN THAILAND
Review round: 1
Reviewer: 2

Output:
Basic reporting: The grammar of the manuscript is not acceptable. There are many sections where I did not understand what the authors were trying to communicate. As an example, consider the first sentence of the abstract. Do that authors mean to imply that the taxonomic uncertainty in this group makes it challenging to infer its biogeographic history? I think so, but the wording is unclear and ambiguous in the first sentence. There are many additional examples.

The figures are clear and easy to interpret. The references are sufficient and appropriate.
Experimental design: The research is clearly within the scope of the journal.

The research question is not clearly define, due in large part to the ambiguities in the written presentation.

The methods description for the molecular biology are adequate.

The methodology for the data analysis is adequate in general. However, there are several small issues that should be addressed:
i. It is inconsistent to use a model of sequence evolution to infer the phylogeny (i.e., lines110-115), but to then calculate genetic distance for use in the other analyses using p-distances (line 128) because substitutions are not corrected in the p-distance as they are in the phylogeny inference. Thus, the same data can produce two different distance matrices.
ii. The Mantel test has been questioned on several levels for inferring isolation by distance. Better options are available (e.g., Legendre P, Fortin, MJ. 2010. Comparison of the Mantel test and alternative approaches for detecting complex multivariate relationships in the spatial analysis of genetic data. Mol. Ecol. Resour. 10, 831-844. AND Diniz-Filho JA, et al. 2013. Mantel test in population genetics. Genet. Mol. Biol. 36, 475-485.)
iii. It is in poor form to use a software package such as DNAsp to conduct an analysis such as the mismatch distribution without citing the original justification for this test [in this case Rogers, A. R., & Harpending, H. (1992). Population growth makes waves in the distribution of pairwise genetic differences. Molecular biology and evolution, 9(3), 552-569.]
Validity of the findings: The general findings appear valid.

The authors appear to have interpreted their results in a reasonable manner.
Additional comments: I believe that this work has a substantial amount of potential. However, I cannot recommend that it be published without a clear improvement in the presentation, and a correction of some of the analyses.


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: PHYLOGENETIC RELATIONSHIPS AND GENETIC DIVERSITY OF THE POLYPEDATES LEUCOMYSTAX COMPLEX IN THAILAND
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Buddhachat and Suwannapoom revised their submission on a phylogeography of frogs belonging to the Polypedatus leucomystax complex occurring in Thailand. They have managed to improve the clarity of their MS but I still thought it somewhat long-winded in places. Below I suggest some cuts to streamline it more. I also have some language/style issues.

Why is the list of five species in line 54 not a subset of the six species mentioned in 50-51? Based on everything you wrote before that should be the case! Also, please keep the order of names consistent (e.g. alphabetical).

Line 51: delimited from >>> distinguished in

Line 56: remove redundant words “A study by”

Line 64: remove “highly”

Line 67-69: remove these sentences, they are out of place here.

Line 76: remove redundant words “In this study”

Line 90: remove “independently”

Line 91: genus name should be abbreviated, it seems you are inconsistent with this throughout the MS

Line 115: remove “population genetics software”

Line 142: could consist >>> consists

Line 149-150: the clade C population >>> clade C

Line 157-158: remove this sentence

Line 162-163: Change sentence to: Haplotypes F and G of clade D are considerably divergent from the rest of clade D and we partition it in two subclades: D1 and D2.

Line 184 and elsewhere: it is quite confusing to call this Northern B rather than Northern D…

Lines 190-198: These sentences are irrelevant, remove. I think spelling out a phylogeny rather than simply referring to the figure that summarizes the info is a bit much for Results already, but there is definitely no place for that in Discussion.

Line 198-199: Although mtDNA seemed to offer cleanly split clades with a unique haplotype in each clade, mtDNA introgession/hybridization between the closely related species can occur. This can
occur particularly in sympatric populations or at the boundaries of species distributions resulting
from incomplete reproductive isolation. >>> Although the mtDNA phylogeny reveals the presence of distinct clades, mtDNA introgression is frequently observed where closely related species are in secondary contact (CITE: (1) Toews DPL, Brelsford A. 2012. The biogeography of mitochondrial and nuclear discordance in animals. Mol. Ecol., 21:3907-3930. (2) Zieliński P, Nadachowska-Brzyska K, Wielstra B, Szkotak R, Covaciu-Marcov S, Cogălniceanu D, Babik W. 2013. No evidence for nuclear introgression despite complete mtDNA replacement in the Carpathian newt (Lissotriton montandoni). Mol. Ecol., 22:1884-1903. (3) Wielstra B, Burke T, Butlin RK, Arntzen JW. 2017. A signature of dynamic biogeography: enclaves indicate past species replacement. Proceedings of the Royal Society of London B: Biological Sciences, 284:20172014. (4) Wielstra B, Burke T, Butlin RK, Avcı A, Üzüm N, Bozkurt E, Olgun K, Arntzen JW. 2017. A genomic footprint of hybrid zone movement in crested newts. Evolution Letters, 1:93-101.)

Line 202-205: For instance, some populations of European newts Triturus montandoni have an mtDNA haplotype of Triturus vulgaris in an area where their distributions are connected, most likely as a result of historical or ongoing hybridization and multiple introgression of mtDNA from T. vulgaris to T. montandoni (Babik et al., 2005). – I think this sentence is too much detail and can be removed. The taxonomy used is outdated and a more recent and more detailed study is a more appropriate citation. See the rewritten sentence I propose above and I suggest to add some (newt) citations relevant citations there.

Line 187-189, 201-202 and 205-207: Merge these sentences and place them after suggested rewrite of lines 198-199 as “Therefore, the use of mitochondria DNA data alone is not sufficient for species delineation. An integrative approach, consulting additional data such as morphology, bioacoustics, ecology, and/or nuclear DNA, would be required to more accurately assess the taxonomy of the Polypedates leucomystax complex (CITE: Padial J, Miralles A, De la Riva I, Vences M. 2010. The integrative future of taxonomy. Front. Zool., 7:16.)”.

Line 207: remove “A recent study by”

Line 207: THE P. leucomystax complex

Line 217: remove “expansion”

Line 212-213: “forms a significant region separating them” >>> “corresponds to a considerable phylogeographic break”

Line 219-220: “we assumed that the northern B clade and the Southern clade might be P. megacephalus and P. leucomystax, respectively” we ascribe the northern B clade to P. megacephalus and the southern clade to P. leucomystax”

Line 221: remarkable >>> considerable

Line 223: to suggest a hypothesis >>> to suggest OR to hypothesize

Line 231: remove “A study by”

Line 236-238 “Additionally, data on rainfall in Thailand by the Thai Meteorological Department indicates a difference in the amount of rainfall between areas to the north and south of the isthmus (Fig. 3).” This does not add anything, remove this sentence and remove the Fig. 3 (which is not convincing).

Line 238: Based on this, we believe that climate may be a >>> We suggest climate was a

Line 240-241: remove this sentence

Line 245: Where does this molecular dating come from? I presume a previous study? Cite it!

Line 247: may be >>> is

Line 250-262: Remove this paragraph. You have linked the phylogeographic break at the IOK to correspond to distinct climate zones, that is enough. This paragraph is highly speculative and confusing and does not help.

Line 272: remove “great”


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: SICEGAR: R PACKAGE FOR SIGMOIDAL AND DOUBLE-SIGMOIDAL CURVE FITTING
Review round: 1
Reviewer: 1

Output:
Basic reporting: See "General comments for the author"
Experimental design: See "General comments for the author"
Validity of the findings: See "General comments for the author"
Additional comments: The manuscript „Sicegar: R package for sigmoidal and double-sigmoidal curve fitting“ by Caglar and coworkers describes an R package that conducts sigmoidal curve fitting and model selection to choose between “sigmoidal”,  “double sigmoidal”, “ambiguous” (no decision can be made) and “no signal” (no growth characteristics) curve structure. The current implementation is based on the following steps: i) normalizing the data within [0, 1], ii) checking for minimum and maximum threshold levels, iii) fitting a sigmoidal and double sigmoidal model by maximum likelihood (nonlinear least-squares) using the minpack.lm package and a grid of starting estimates for robustness, and finally iv) model selection based on lowest AIC. This algorithm is tested by an extensive simulation regime, in which increasing noise is added to perfect sigmoidal/double sigmoidal models (“ground truth”). It could be demonstrated that with the exception of extremely high noise levels, the implementation succeeds in identifying the underlying true model.
The manuscript is well-written and the package works well, however there are some important points the authors should address before rendering it suitable for publication.
1)	It is not really clear - and nowhere mentioned - in which scenario (biological, pharmaceutical or clinical question) the selection between sigmoids/double sigmoids is essential. This information (maybe discriminating growth from growth with subsequent decay) should be supplied in the “Introduction”; else, the readership will see no real-world application.
2)	AIC is not explained and not written in unabbreviated form.
3)	When drawing the starting parameters from a uniform distribution (line 49), does it make sense to draw random values from it? Functions such as runif might miss some essential values. Would it not be better to create a sequence from within this window, i.e. seq(lower, upper, length.out = 100) to ensure that the complete parameter space is employed?
4)	The authors should at least verify that the quality of model selection is also achieved when i) the predictor values are not an equidistant sequence (3 to 30, in 0.5 increments) and ii) the noise setup is heteroscedastic, i.e. noise is a function of the magnitude. This must not necessarily be included as a figure, but the outcome would be interesting as most of the real-world data does not have constant (homoscedastic) noise.
5)	It would also be interesting to know how the model selection performs when the authors use a 5-parameter (Richards) sigmoidal model, which often fits better when the curve is asymmetric.
6)	In lines 172ff, the authors describe a decreasing performance of model selection in a high-noise regime. In this context, the authors should cite the work from Spiess & Neumeyer (https://bmcpharma.biomedcentral.com/articles/10.1186/1471-2210-10-6), which investigated model sigmoidal model selection and resulting goodness-of-fit measures at varying noise levels.
7)	I strongly believe that Fig. 1 and Fig. 2 could be merged into one concise Figure, i.e. the different phases of the double-sigmoid could be denoted in Fig. 2B.
8)	The authors have completely neglected the drc package, which also offers a wealth of functionality for sigmoidal dose-response curve fitting and model selection. It should be cited.


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: SICEGAR: R PACKAGE FOR SIGMOIDAL AND DOUBLE-SIGMOIDAL CURVE FITTING
Review round: 1
Reviewer: 2

Output:
Basic reporting: 1) The introduction would need to be improved: it is simply too short (one (self) citation is not enough).

The authors need to provide background paragraphs on 1) existing (statistical) methods for fitting (nonlinear) s-shaped data (e.g., generalized linear and nonlinear regression) and 2) (more importantly) existing software for fitting s-shaped data. There are several R packages that should be mentioned: drc, drfit, grofit, qpcr, some of which are mentioned in the later subsection in lines 188-205; these lines should be integrated into the introduction. Note that the R package "drc", which can also fit biphasic patterns just like the proposed double sigmoidal model, is widely used for analysis for many different types of data.

2) There are several claims throughout the manuscript that would need to be substantiated by suitable references, e.g., lines 21-23, 25-26, 64 (Why these thresholds?), 132 (Fermi?), 159-160 (Any reference for this definition as it's an unusual definition. Usually such a range would be defined based on a range on the y axis, e.g., EC5 to EC95).

3) Definitions and methods are placed in the Results section. Please consider re-arranging parts of the material in the manuscript, e.g., lines 107-164 should be placed in the Methods section. On the other hand lines 124-131 are very relevant in the Discussion.

4) Please do not repeat definitions and methods used in the Results section, e.g., lines 182-183. Typo: "insure" should be "ensure".
Experimental design: The manuscript addresses the problem of fitting high-throughput s-shaped data by providing an R package that allows classification of such data into 4 categories (including two types of nonlinear patterns) depending on the signal in the data. This is an interesting but also challenging problem.

Moreover, it seems that a novel multiplicative double sigmoidal model has been proposed although there could be links to models for independent action of mixtures.

However, some claims should be omitted: In lines 123, 132 it's claimed that any sigmoidal curve is fully determined by 3 parameters. This is simply not correct in general. There exist both four and five-parameter models for s-shaped data. Please look into the literature on logistic or log-logistic models. Actually, the authors define a four-parameter model in the appendix! Confusing.

In lines 59-60: Perhaps I don't understand, but why should the AIC be larger than -10? Depending on the data AIC can take on arbitrary values I believe. A sensible rationale (a reference?) need to be supplied for such a non-standard rule.

It would also be helpful if the authors could specify the probability distribution that is assumed when fitting models using maximum likelihood (line 47). Is it least squares estimation?
Validity of the findings: The proposed R package performs as would be expected: the more noise the more difficult the classification. This is nicely shown in Figure 3.

Would it be possible to include a real application? It is always to good to see a methodology used in practice.

The authors need to provide a short conclusion summarizing their findings and, possibly, experiences using the R package. Also, if no real data example can be provided, it should be mentioned as a limitation (as then it would seen that the package has not been used much in practice; good to know for potential users).

Note also that high-throughput data may be very heterogeneous, being a mixture of data with various noise levels. It seems that this realistic setting has not been explored for the R package "sicegar".
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: SICEGAR: R PACKAGE FOR SIGMOIDAL AND DOUBLE-SIGMOIDAL CURVE FITTING
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment
Additional comments: The authors have adequately addressed all raised points and the manuscript is now suitable for publication. I especially liked the now included thorough analysis of the different noise regimes.
One small grammar issue: Line 280: Unlike sicegar, ...


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: SICEGAR: R PACKAGE FOR SIGMOIDAL AND DOUBLE-SIGMOIDAL CURVE FITTING
Review round: 2
Reviewer: 2

Output:
Basic reporting: The manuscript now complies with rules of basic reporting.
Experimental design: More details and explanations have been included. The manuscript reads well now.
Validity of the findings: A data example has been included, providing added value to the manuscript. All results (real data and simulations) fit together.
Additional comments: The manuscript is much improved (a detail: make sure poliovirus is written the same way throughout the manuscript). No further comments.