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

Input:
Title: GENOME SIZE VERSUS GEOGRAPHIC RANGE SIZE IN BIRDS
Review round: 2
Reviewer: 3

Output:
Basic reporting: I feel this version of the manuscript is improved and is now more than adequate.
Experimental design: I feel the analysis is rigorous. There are intrinsic limitations to the data the authors analyze, which they describe in a section called "Study limitations". I like this quite a bit. Overcoming these limitations (e.g., geographic biases; the problems remaining in avian phylogenies) would require another decade of data accumulation (e.g., more information from tropical species, better megaphylogenies). This is an interesting story and will push the field forward; the authors should be able to publish this now and not wait for "perfect data".
Validity of the findings: I believe the findings are valid. I provide additional details above in section 2 "Experimental design"
Additional comments: I really liked this revision. I feel that you carefully considered and addressed the my comments and the comments made by by the other reviewers.

I debated an accept vs minor revisions recommendation. I have one minor recommendation related to Fig. 1. I really love the new Fig. 1 -- I believe that it conveys very important information to readers. However, I do have one minor criticism. The authors state "It is very difficult to locate these orders in the phylogenetic tree by Jarvis et al. (2014) or Ksepka et al. (2020). Therefore, we trimmed Jetz et al. (2012, 2014) tree and plotted summary statistics for bird orders."

I understand this and it is reasonable response. This figure is largely to orient readers rather than an effort to provide phylogenetic control. However, I think the authors should (minimally) change the Fig. 1 legend or (ideally, in my opinion) revise the tree. Specifically, the legend is:

"Figure 1
A consensus phylogenetic tree and studied variables
Bars are means with standard deviations. Sample size (number of species) is given next to each bar. NA indicates that data was not available"

At the absolute minimum it should acknowledge that this tree is the Jetz et al. tree.

However, I would like to point out that there is a modern tree that includes all avian orders and meets the criterion of being the result of analyses using phylogenomic datasets - it is Kimball et al. 2019. The Kimball et al. 2019 tree is a supertree - a meta-analysis of trees based on large-scale phylogenetic studies (most source trees were based on 1000's of loci). The Kimball et al. tree is (unsurprisingly) very similar to the Jarvis et al. 2014 tree where they overlap. It seems to me like the ideal solution for Fig. 1. I provide a full citation below. All orders that the authors show in their Fig. 1 are in the tree shown as Figure 3 of Kimball et al. 2019. In retrospect, I should have pointed the authors to this tree. Note also that Fig. 1 of their paper would be fine as a cladogram (i.e., a tree without meaningful branch lengths; in fact, I think a cladogram would be better than what they have).

Kimball, R.T.; Oliveros, C.H.; Wang, N.; White, N.D.; Barker, F.K.; Field, D.J.; Ksepka, D.T.; Chesser, R.T.; Moyle, R.G.; Braun, M.J.; Brumfield, R.T.; Faircloth, B.C.; Smith, B.T.; Braun, E.L. A Phylogenomic Supertree of Birds. Diversity 2019, 11, 109. https://doi.org/10.3390/d11070109

In the interest of full disclosure, I want to call the authors' (and editor's) attention to the fact that I am a co-author of Kimball et al. 2019. I. recognize that this is a touchy issue and I try to avoid recommending a citation to my own work unless I feel it is absolutely critical. That is why I have provided an alternative in this review. With that said, I hope that the authors will carefully consider using the Kimball et al. tree; it is a modern tree and I will stress that both I and one other review commented on the issues with the Jetz tree.

I really hope that this paper is ultimately accepted. In my opinion, it will be an important contribution to the literature.

Edward L. Braun
Professor of Biology, University of Florida


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: EXPLORING THE OCCURRENCE OF THIOFLAVIN-T-POSITIVE INSULIN AMYLOID AGGREGATION INTERMEDIATES
Review round: 1
Reviewer: 1

Output:
Basic reporting: No issues
Experimental design: No issues - except that the experimentation could be expanded (see general comments)
Validity of the findings: Also fine
Additional comments: Smirnovas and coworkers undertake to examine a curious but not very diligently reported phenomenon: deviations from sigmoidal behavior in fibrillation. All scientists working with fibrillation kinetics experience these uncanonical time courses, yet they are (speaking from personal and collegial experience) invariably disregarded as inexplicable outliers that defy closer analysis. From that perspective alone the authors are to be commended for trying to address such elusive phenomena.
Major point: Unfortunately I am not really left much wiser from their labours (and therefore not convinced that I or my colleagues should abandon our dismissive attitudes towards such time profiles). The authors do not show any major effect of the non-sigmoidal curves on the fibrillar outcome and do not connect the intermediate species with any specific features. This is actually a pity since it would be interesting to investigate if the intermediates that apparently accumulate midway between the two inflection points have specific properties distinct from what might be observed from simple sigmoidal kinetics. I think the study is of interest for fibrillation researchers simply for following through on this phenomenon – but perhaps mainly to confirm that these phenomena are not particularly important. Unless the authors can show that there are species accumulating along the way of the non-sigmoidal pathways (and not along the sigmoidal one) with distinct properties (e.g. in terms of vesicle permeabilization or cell toxicity etc) it will merely be a calming note telling us not to concern ourselves too much about these aberrations.
Other points:
1.	The last sentence of the abstract is not complete. “how it affects…” – what is “it” here and what is the actual conclusion? So far it is just a description of some observations.
2.	Introduction line 30: Technically Tafimidis is available against aggregation of transthyretin in Familial amyloidotic polyneuropathy which is considered a neurodegenerative disease.
3.	Line 89: “differences from distinct dye binding”. Presumably the authors mean if the ThT fluorescence behavior indicate differences that are not related to dye binding but this should be clarified and some possible alternatives to binding be indicated.
4.	The authors should provide details on how the ThT stock solution was prepared – was it simply dissolved in water?
5.	Fig. 4A: The y-axis should not be time – that is the x-axis. It is presumably the maximal ThT emission value.
6.	Lines 228-230: “Such lines can be caused by either a large particle floating past the optical path during a scan or by sudden association and dissociation of a ThT-positive aggregate.” This sounds extremely stochastical. Is this based on a single observation or multiple ones? It is unclear (both from Results and Discussion) whether the data in Fig. 4 are based on a single double-sigmoidal run or has been observed on multiple occasions.


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: EXPLORING THE OCCURRENCE OF THIOFLAVIN-T-POSITIVE INSULIN AMYLOID AGGREGATION INTERMEDIATES
Review round: 1
Reviewer: 2

Output:
Basic reporting: This manuscript by Ziaunys and co-workers is written clearly, and the Introduction and Background provide proper context for the study. The literature references are appropriate. The structure of the manuscript conforms to the discipline norm. The figures are well made, although I think that the y-axis in panel A of Figure 4 is probably mislabeled (both the x- and y-axes are labeled “Time (min)”). The raw data are supplied. I have two minor comments about the introduction:
a.	In the first sentence of the abstract the authors state “The assembly of proteins into highly structured amyloid fibrils is considered to be the main cause of several neurodegenerative diseases”. This statement is highly debatable. Certainly, the process of aggregation seems to drive pathogenesis in many neurodegenerative diseases, but the specific role of amyloid fibrils is disputed as discussed in the Knowles Nat Rev Mol Cell Biol 2014 review that the authors cite. I would suggest changing the wording of this sentence to “The aggregation of proteins is considered to be the main cause of several neurodegenerative diseases”.
b.	In lines 29-30 the authors state that there are no disease modifying drugs available for amyloid diseases. However, several drugs are now available to treat the transthyretin amyloidosis (tafamidis, diflunisal, inotersen and patisiran).
Experimental design: The manuscript describes original primary research. The research question, which is to probe the kinetics of amyloid formation by the model protein insulin, is well defined and it is clear how it relates to previous research in the field. The work is generally technically sound. I particularly like the authors’ approach to study the appearance of double sigmoidal kinetics as a rare stochastic event, rather than trying to eliminate it or emphasize it by manipulating experimental conditions. However, I have the following comments:
a.	I think that the authors should state clearly the number of distinct samples they examined by AFM to clarify how representative the images are of the contents of their insulin amyloidogenesis reactions.
b.	I think the authors should show a representative AFM image of a sample that manifests single sigmoidal kinetics just before the growth phase begins (perhaps around the 250 minute time point) so that it can be compared to AFM image from the equivalent time point in double sigmoidal reactions that is represented in Figure 3A. Such data is needed to understand whether the species formed during the first sigmoidal phase in double sigmoidal aggregation reactions are different from those that exist in single sigmoidal reactions pre-growth phase.
c.	The authors should mention what kind of AFM they used- I could not find this information in the Experimental section.
d.	I think the authors may be making too much of the spike in fluorescence they observed in the data from the double sigmoidal reaction in Figure 4A, given that it seems like they only observed it in the one sample represented in this figure. The authors need to repeat this experiment, preferably in triplicate at least, or if they were replicated, they should be clear about how many replicates are represented in the figure.
e.	The supplemental data for the excitation/emission matrices should be labeled so that it is clear which time points they correspond to.
Validity of the findings: I found the authors results to be sound except for the minor points noted above. Their conclusions are supported by their results and their speculation as to the meaning for the broader field of amyloidosis is appropriate and reasonable.
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: BACTERIAL COMMUNITY DIVERSITY, LIGNOCELLULOSE COMPONENTS, AND HISTOLOGICAL CHANGES IN COMPOSTING USING AGRICULTURAL STRAWS FOR AGARICUS BISPORUS PRODUCTION
Review round: 1
Reviewer: 1

Output:
Basic reporting: Song et al report a systematic and detailed study of degradation/composting of agricultural residues in term of lignocellulose composition, bacterial community diversity and morphological changers as a function of time. Study is very interesting and useful in understanding the bioprocessing of agricultural straws and usage of composting products in cultivating other edible/agricultural products including mushrooms.

The study is clear and unambiguous. Manuscript is clearly written.
Experimental design: Rigorous investigation performed to a high technical & ethical standard.

Methods described with sufficient detail and information to replicate.
Validity of the findings: All underlying data have been provided

Data is robust, statistically sound, and controlled

Conclusions can be improved by adding more detail about the application of the current study.
Additional comments: In the introduction section, I suggest adding more detail about the time required for composting preparation and how the current study could help a biotechnology industry.

Specific points:

1.	It is very unclear how the temperature variation affects microbial community composition. Authors mentioned the microbial composition and temperature as a separate entity. A figure showing the “temperature vs biological community enrichment can be very helpful in understanding the importance of temperature in enriching a biological community diversity.
2.	Figure 2. It is hard to follow so many parameters. Define “CS, WS, RS, CC, C and B” in the figure legend. Also define Y-axes N and C/N ration in the figure legend.
3. Table 1. Describe CS, WS, RS, CC, C and B.
4. Conclusions can be improved by adding more detail about the application of the current study.


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

Input:
Title: BACTERIAL COMMUNITY DIVERSITY, LIGNOCELLULOSE COMPONENTS, AND HISTOLOGICAL CHANGES IN COMPOSTING USING AGRICULTURAL STRAWS FOR AGARICUS BISPORUS PRODUCTION
Review round: 1
Reviewer: 2

Output:
Basic reporting: A lot of grammar, spelling, and punctuation usage can be improved for example in line 35, 37, and 47-49. I would suggest getting the manuscript edited by a native English speaker.

Line 142: I was unable to find the reference cited here: Cao et al. 2019. Please make sure all the cited references are included in the References section.

Fig. 3 and Table 1: The usage of small alphabets statistical differences is hard to understand. Please use conventional asterisks or provide p values for each significantly different pair.

In the interest of readers from diverse background, I suggest expanding some of the abbreviations like C, N, P, K, RS, WS, CS etc. Use them in their full forms throughout the manuscript. It would also prevent mistake like “RC” instead of “RS” in line 289.
Experimental design: Lines 125-126: There seems to be a mistake in defining biological efficiency. It cannot be the ratio of T3 to TY. It should be the ratio of fresh mushroom weight to the weight of dry substrate.

Line 125: Elaborate if T3 is the weight of 1-3 flushes combined or is it average of all the three flushes. It may be helpful to include values for each of the three flushes in Table 1.
Validity of the findings: Line 266: Please elaborate what does this sentence signify “The N concentration in mature compost seems related to the mushroom yield”.
Additional comments: The manuscript by Song et al. describes the properties and characteristics of 6 different agricultural straws used for the production of mushroom. The authors compared different AS for their physico-chemical properties and analyzed changes throughout the fermentation process. They also sequenced and compared the microflora among these different AS. Based on their data, they recommend the AS from WS, RS, and CS to be most suited for mushroom production.
The results are exciting, however I have some minor queries.

Fig. 2A: It would be interesting to see a line graph of changes in C/N ratio among different stages of fermentation.

Line 33: The sentence is incomplete without mentioning how much AS are produced worldwide annually.

Line 44: please change “American” to “America”.

Table 1 and S3: Define “EB”. Is it same as biological efficiency (BE)?

Line 23: Please change “Phage” to “Phase”.


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: BACTERIAL COMMUNITY DIVERSITY, LIGNOCELLULOSE COMPONENTS, AND HISTOLOGICAL CHANGES IN COMPOSTING USING AGRICULTURAL STRAWS FOR AGARICUS BISPORUS PRODUCTION
Review round: 2
Reviewer: 1

Output:
Basic reporting: I have no further comments.
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Most of the comments have been answered by the authors. I am however not satisfied with the line graph added to Fig. 2A. The line graph is for which of the 6 agricultural straws? Please elaborate or add line graphs for all the 6 AS.


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: A RISK SCORE MODEL WITH FIVE LONG NON-CODING RNAS FOR PREDICTING PROGNOSIS IN GASTRIC CANCER: AN INTEGRATED ANALYSIS COMBINING TCGA AND GEO DATASETS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors' attempt and purpose to build a risk prediction model in the context of Gastric Cancer seems logical and clear as such type of models is not uncommon in biomedical research. They seek to aid clinicians and patients to undertake better decisions about GC
treatments.
Experimental design: All data sources, statistical packages, and computational models are explicitly named in the paper and available for the study replication. Overall, the data and methods parts are adequately presented and easy to follow.  The research is multistep describing each part in sufficient detail across the article. The statistical methods include Bayesian analysis, Cox regression and Kaplan-Meier all of which are frequently applied in biomedicine and seem appropriate for performing their respective tasks at different stages of the project to create a scoring model and identifying important gastric cancer gene-related biomarkers. Every R package used in the study is specified, making it easier for other researchers to reproduce the study. Even though the methodology and data are clearly described in the article, the whole text will benefit from proofreading to eliminate typos and various
grammatical issues that appear across various sections including Figures. Nevertheless some presentations of methods I found a bit difficult to grasp, despite knowing something about their practical application.
Validity of the findings: 1.     More information should be provided on why the authors bounded the OS and DFS at 48 and 24 months respectively. The description: “the curve tends to be gentle” (line 138) is subjective. There is still at least a 10% decrease in both survival curves after those bounds (Figure 1 C-D).

2.     Survival curves (figure 1-4) should include a confidence interval. This is specifically important given that the size of the datasets is small.

3.     It is not clear how the authors concluded that the small sample size in stage (1) patients is a limitation (line188) without carrying out a power analysis.

4.     Table 2: showing a representation of the workflow; somehow lacks the univariate cox proportional hazard regression analysis which is
described (line 129).

5.     Table 2: layout should be modified as the directions of arrows follows a snake-like structure making it difficult to read. In addition, each rectangular box could be numbered to improve reading simplicity.

6.     Table 3:  number of patients doesn’t match the text i.e. (line 189) says that a number of patients in stage I is 26, yet table 3 shows that stage I has 14 high and 41 low-risk patients. Please clarify

7. Age cut off for Old / Young is not specified (would be good to have
clarification).

8. P-value was adjusted (good to have clarification on how they were adjusted).

9. Figure 7: how the top 10 enrichment pathways were selected?

10.     It might be more informative to include the clinical information
for each cancer stage separately in table 3.

11. Could be explained how the Kyoto Encyclopaedia of Genes and Genomes was combined with the Web-based Gene set analysis toolkit to analyse the aberrantly activated signalling pathways.

Also important to mention that the deficiencies in the statistical applications are only succinctly mentioned by the authors. In my view, it could have been identified in the article more meaningfully. Expanding it specifically to statistical methods as well as broadly
discussing the shortcomings of data would make the paper more valuable.
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: A RISK SCORE MODEL WITH FIVE LONG NON-CODING RNAS FOR PREDICTING PROGNOSIS IN GASTRIC CANCER: AN INTEGRATED ANALYSIS COMBINING TCGA AND GEO DATASETS
Review round: 1
Reviewer: 2

Output:
Basic reporting: 1.LncRNAs and gene mentioned in the materials, methods and results section of the paper may express the same meaning. It is suggested to explain clearly and avoid confusion.
2.Please provide the lists of 278 lncRNAs and 38 shared genes in the supplementary materials.
3.Please correct the spelling mistakes such as time-dependent and forest plot.
4.Figure 1B is not clear and please add the legend to explain it.
Experimental design: 1.Please confirm the the cut-off value of high and low risk groups is the median or zero score in Figure 2C-D and 3C-D further.
2.How are 408 samples screened from the TCGA STAD database?
3.DFS data of GSE62254 dataset is available from the supplementary materials of the article (Molecular analysis of gastric cancer identifies subtypes associated with distinct clinical outcomes), why is it not verified?
4.Please provide the details of the risk score model and the risk score of each patient to explain the range of risk score (-2.5-2.5) in the nomogram model.
Validity of the findings: 1.Please provide the multivariate cox analysis form of TCGA data.
2.The coefficients of 5 lncRNAs do not correspond to the HR values in Table 1.
3.The sample sizes of the scatter plot (n = 300 and 140) are not consistent with that of data sets (n = 300 and 200) in the validation groups.
4.It is recommended to give the ROC analysis of 1-4 years cut-off OS and 1-2 years cut-off DFS.
5.In Figure 7A, the absolute value of Pearson correlation coefficient should not be greater than 1.
Additional comments: The article showed a risk score model combining five-lncRNA signature to predict the prognosis of GC patients, while there were still some work remaining to be improved.


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

Input:
Title: A RISK SCORE MODEL WITH FIVE LONG NON-CODING RNAS FOR PREDICTING PROGNOSIS IN GASTRIC CANCER: AN INTEGRATED ANALYSIS COMBINING TCGA AND GEO DATASETS
Review round: 2
Reviewer: 1

Output:
Basic reporting: 1. There are still inconsistencies in the paper that need to be addressed. For instance in lines 175-176 “OS and DFS in test cohort (Fig. 2A-B)”, but figure 2 description “(A-B)
Kaplan-Meier analysis of patients’ overall survival and disease-free survival in the high-risk (n = 204) and low-risk (n = 204) subgroups of the training set.” It should be clarified to whether the graphs and figures are obtained from the training or test dataset.

2. Even though the paper has been proofread, further work is still required. For eaxample: line 243 “differented” and line 258 “socring”. There are also inconsistencies with the words used: line 182-184 author uses “cut-off”, but in lines 108 and 116 “cutoff” is used instead. Another example is with the word dataset: line 340 “datasets” but in line 341 author uses “data sets”. There are similar mistakes within the text that should be carefully reviewed.
Experimental design: 'no comment'
Validity of the findings: The validity of finds is appropriately, and it's evaluated on an
external dataset (GEO).
1. The paper would benefit if it included metadata on all patients, not only the ones in the training cohort, as seen in Table 3.

2. The discussion section should consist of more information regarding the limitations of the study/datasets and how it would be possible to improve them in the future.
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: A RISK SCORE MODEL WITH FIVE LONG NON-CODING RNAS FOR PREDICTING PROGNOSIS IN GASTRIC CANCER: AN INTEGRATED ANALYSIS COMBINING TCGA AND GEO DATASETS
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment.
Experimental design: Please confirm the the cut-off value of high and low risk groups in Figure  3C-D further.
Validity of the findings: According to the risk score model, how to understand the risk score ranges from -2.086959745 to 2.270305234？
Whether LINC00106 plays an important role in the model？
Additional comments: The article showed a risk score model combining five-lncRNA signature to predict the prognosis of GC patients, while there were still some work remaining to be improved.


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

Input:
Title: EVALUATION OF RESISTANCE TO WHEAT STEM RUST AND IDENTIFICATION OF RESISTANCE GENES IN WHEAT LINES FROM HEILONGJIANG PROVINCE
Review round: 1
Reviewer: 1

Output:
Basic reporting: Well-written manuscript with suffiencient background and context provided.
Needs additional work on Results and Discussion sections.
Experimental design: Overall, the experiments are well-conducted, and the results are consistent with the experimental design proposed.
Validity of the findings: Please, read general comments for author.
Additional comments: October 6, 2020

Dear Editor of PeerJ journal,

Thank you so much for referring me the manuscript #52649, entitled ‘Evaluation of resistance to wheat stem rust and identification of resistance genes in wheat lines’. This research addresses a relevant topic, which is the understanding of the basis of stem rust resistance in breeding materials. Getting to know what genes are present in a breeding program is crucial for deciding the breeding strategies to combine effective genes to guarantee long-lasting resistance.

This research includes stem rust phenotyping at the seedling and adult stages against three Chinese races of the stem rust pathogen, and a molecular evaluation for the presence of six Sr genes in 95 breeding lines. Overall, the experiments are well-conducted, and the results are consistent with the experimental design proposed. However, I think this manuscript needs more elaboration and additional interpretation of the results that will definitely enrich both the Results and Discussion sections.

I am including here the major points that were missing or need to be reviewed:

1)	A strong emphasis was put in this manuscript on finding resistance to Ug99. Based on your evaluation, you cannot conclude that your resistance will be effective against Ug99 races. The races you used here are different from Ug99 in terms of virulence. None of the three races you tested are virulent on Sr31 or Sr38 (critical virulences in Ug99 races). You can only conclude that your genes will be effective against Ug99 races if you evaluate your germplasm against these races. So, you need to emphasize that although these lines proved to have good resistance to the three races you used, their effectiveness against Ug99 races will be only determine once they get evaluated against Ug99 or proven by molecular markers that they carry genes that are effective against Ug99. If your original objective was to find lines that are resistant to Ug99 races, unless you run markers for additional genes that are effective to Ug99, you will not be able to address it.

2)	There is an important missing point in relation to Sr24. If you see the three races you used in your study, all of them are virulent to Sr24. So, this gene is truly not a good option in your province. Maybe, the reason why you don't have Sr24 in your materials is that it is not a good gene in your province and was selected against by the virulent races. In your discussion (lines 216-217) you mentioned that Sr24 provides resistance to most Chinese races, but the three races you used in your research are virulent on Sr24. If you add a race avirulent on Sr24 in your seedling evaluations, you would be able to postulate this gene easily.

3)	No discussion was made about the narrow basis of stem rust resistance in these materials. Only three Sr genes were identified with molecular markers: Sr2, Sr31, Sr38. And although these have been relevant genes used to protect wheat from stem rust for many years and are still effective in China, now virulence to these genes is becoming more frequent and are not that effective anymore. Need to add in the discussion that more genes need to be evaluated through the use of molecular markers. Will give you a better picture of how diverse your breeding material in terms of stem rust resistance is. Based on the phenotypes observed it does not seem to be highly diverse.

4)	I was expecting to read what will come next after this research. Recommendations from this group about how to continue this research to better understand the basis of stem rust resistance in these highly resistant lines. Running markers for additional Sr genes? What criteria to select lines for stem rust improvement? Pyramiding genes (Sr2, 31, and 38 to protect from Chinese races + additional genes to protect from Ug99??)

5)	No analysis was made to correlate the phenotypes and the markers data. Do the lines carrying Sr31 or Sr38 (or a combination of both) perform better than the lines that do not have them? Same for Sr2.

Additional edits:

Lots of missing citations in the Discussion section (I highlighted them).

Review the table's numbers. Not matching between tables number and manuscript body.

Title: I would add the origin of these lines (Heilongjiang province) at the end of the title.

Line 18: change ‘detected’ to ‘evaluated’.

Line 33: add ‘effective’ before ‘stem rust resistance genes’.

Lines 40-44: Needs a better description of the Ug99 race group, and how new variants in the group has emerged. Ug99 was first identified in Uganda in 1998 (Pretorius et al, 2000), and was race-typed as race TTKSK in 2006. Race TTKSK is virulent on both Sr31 and Sr38, making this virulence combination so significant. New variants of Ug99 with additional virulence on Sr24 (TTKST), Sr36 (TTTSK), and SrTmp (TTKTT and TTKTK) were identified since then (see Newcomb et al., 2016). But also, there have been new variants occurred that report a loss in virulence, like on Sr30 (TTHST). Although races in the Ug99 group are virulent and a big threat, they have not caused any epidemic, except for Kenya. The race group has been spreading, reaching 13 or more countries, but no epidemics were reported due to Ug99 other than big losses in Kenya.

Line 48: race TTTTF was wrongly called in Bhattacharya’s paper. The correct name of the race is TTRTF (See Patpour et al., 2017 and Olivera et al., 2019).

Line 54: Sr13 and Sr21 are not APR genes. They are both affected by temperature, but they are both all-stage resistance genes.

Line 75: change ‘Sr1RS’ for ‘Sr1RSAmigo’.

Line 83: Can you please elaborate more about when these pandemics occurred? Are they recent pandemics? Happened a long time ago?

Lines 105-106: Is it the virulence spectrum the only criteria for the selection of these races? Are these races prevalent in China?

Line 107: what international system of nomenclature are you referring to? I believe it is the North American system based on the race name. Please, you need to cite this.

Line 110: I don't think it is necessary to mention who did this evaluation. Please, eliminate the sentence.

Line 118: change ‘LC’ to “Little Club’

Line 119: change ‘investigated and recorded’ to ‘assessed’

Line 122: Field stem rust evaluation section. There is important information that is omitted here. Did you run three independent single-race nurseries? Or you run only one nursery and you bulk the three races for the inoculum? Based on your Table 2, seems like you had three independent races. This needs to be clearly stated in this section.

Lines 126-131: When you describe the field evaluations, it is not clear how you used the susceptible control LC. Did you use it as an inoculum spreader row? You only mentioned here that you inoculate your wheat lines, but nothing is mentioned about inoculating the susceptible control.

Line 137: I recommend changing the title of this section. It can be: Molecular markers evaluation. Please, mention that you run the six markers in your 95 advanced wheat lines.

Line 152-156: You mentioned here that 9 lines were susceptible to all races and the remaining ones resistant to all races at the seedling stage. This is not what Table 2 is showing. Lines like Jiusan07-6205, Longfu09-1249, Jiusan07-7371, Hong09-558, Nong11-2110, Longfu09-534, Longfu10-848, all of them show race specificity in the seedling responses. Please, check that and elaborate more in this results section.

Line 159: Before you said that the field evaluations were in 2016 and 2017. Please check. Results are presented in table 2 instead of 1, please check.

Lines 159-164: nothing is mentioned about the race specificity in the field response (same as in seedling).

Lines 165-166: Please, clarify what you mention in this sentence. Results appear to correlate very well in both years for each race.

Line 167: ‘Molecular identification’ section. This is a results section. Here, you are presenting a lot of information about each marker that does not fit with this section. All the information describing the markers should go in the Materials and Methods or in the Discussion section.
Also, nothing is mentioned about the lines that carry multiple resistance genes.

Line 199: Review the sentence, it is not correctly written.

Line 200-201: You need a citation for this sentence.

Line 213-215: This sentence needs to be revised. Yes, Sr24 confers resistance to Ug99 (TTKSK), but was added in the differential set after a new variant of Ug99 (TTKST) gained virulence on Sr24.

Lines 216-217: The race that caused the epidemic in Italy is race TTRTF. Please, add citations to this sentence.

Lines 228-230: Please, add citations to these sentences.

Lines 238-239: Please, add a citation to this sentence.

Table 2: For two lines (Pinzi96860 andPinzi96864) you wrote that Sr32 was confirmed with markers. There should be a typo, please check.

Supplemental Table 1.
It seems like the three races used are named based on the North American differential set and nomenclature system. When you present the data, instead of listing the genes in number order, it is clearer if you order them based on the 20 differential sets (Sr5, Sr21, Sr9e, Sr7b … etc.). List first the 20 genes in the differential set and then continue with the additional genes you evaluated.


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: EVALUATION OF RESISTANCE TO WHEAT STEM RUST AND IDENTIFICATION OF RESISTANCE GENES IN WHEAT LINES FROM HEILONGJIANG PROVINCE
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: This manuscript entitled “Evaluation of resistance to wheat stem rust and identification of resistance genes in wheat lines” provides essential information on the stem rust resistance available in Heilongjiang Province. The manuscript is well written in terms of Introduction, research questions, experimental design, and data analysis. It is understood that resistance is available against the predominant local races of Puccinia graminis f. sp. tritici (Pgt), however, it would be nice to see some discussion on strategies to increase resistance sources to Ug99 strains.

I also see need of careful revision in some parts of the manuscript, some of which have been listed below.

“International Center for Agricultural Research in the Dream Areas (ICARDA)” change to “International Center for Agricultural Research in the Dry Areas (ICARDA)”

“some confer non-specific resistance” change to “some confer race non-specific resistance:”.

I would suggest using “combined” instead of “polymerized”.

Some corrections are needed in References.

Change “Bhattacharya S. 2007” to “Bhattacharya S. 2017”

In figure 1, the first lane should be changed to “Marker2000”.

Please check if the Table numbers match with the text.

Please take a look at the edits in the PDF.

Thank you.


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: TRANSCRIPTOME ANALYSIS REVEALS THE MECHANISM OF IMPROVING ERECT-PLANT-TYPE PEANUT YIELD BY SINGLE-SEEDING PRECISION SOWING
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: RNA sequencing experiments should contain three biological repeats for each treated sample.Data from only one test is not appropriated for publication, but could work as a hint of the research.
Validity of the findings: The transcriptomic data can provide a possibilty of the biological question.In the manucript, the authors found that the expression  of resveratrol synthesis genes were induced in peanut roots by single-seed precision sowing and they determined the level of resveratrol. These findings showed that the  resveratrol synthesis was enhanced in the roots by single-seed precision sowing. However, whether its enhance is associated with the germinaltion  and growth of peanuts remain unclear. Also, resveratrol contributes to stress of adaptation of plants needs solid evedence.
Additional comments: The manuscript described a comparative transcriptomic results. The auhours found that the expression  of resveratrol synthesis genes were induced in peanut roots by single-seed precision sowing and the level ofresveratrol was increased in the roots with the same treatment. It may not the mechanism of the increase of peanut germination and growth.
1) The bar is missed in Fig. 1a, and a statistic test is lacking in Fig.1b.
2）The error bars were lost in Fig 2C(?）。
3）Fig. 3a can be shown as a bar chart.
4) Words in Fig. 5 were not clear.
5) No statistic test data in Fig 7.


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: TRANSCRIPTOME ANALYSIS REVEALS THE MECHANISM OF IMPROVING ERECT-PLANT-TYPE PEANUT YIELD BY SINGLE-SEEDING PRECISION SOWING
Review round: 1
Reviewer: 2

Output:
Basic reporting: Intro and Background-
1.	In the abstract, a statement about the relationship of resveratrol to stress is needed. The authors should tie in the role of resveratrol in managing plant stress, lines 75 and 76.
2.	Consider comparing typical sowing methods in China to practices in the US and other peanut growing regions, lines 92 and ff in the introduction. This would give context and wider application to the scientific community at large.
3.	The paragraph describing stress and previous research is lacking in fully developing the relationship between previous research, genes and methods, lines 103-109. This entire section should be revised and improved upon.
4.	On line 109, a new section describing the importance of aflatoxin contamination and resveratrol is included. I would suggest beginning a new paragraph here especially if the first part of the section is more detailed.
5.	The authors should tie in the importance of resveratrol in aflatoxin reduction or leave that out. Clarification is needed, lines 109-113.
6.	Qualify “higher content”, line 116.
7.	Clarify importance of gene discussion to project aims, line 127.
8.	At the conclusion of the intro and background, the authors should describe the purpose of the research, hypothesize about the findings of increased expression of genes to SS planting efficiency and plant viability, and describe how these findings will be used to assess results, after line 148. This is of primary importance in communicating the scientific findings of the research.

Figures-
For most of the figures and tables included in the packet, there is insufficient information. For example:
1.	Figure 1a- which picture is from a SS treatment and which is DS? There should be a description of how the pictures relate to the data shown in part b.
2.	Figure 4- there should be a legend for the colors showing in part a. How do the colors relate to quantity? The gene ID numbers should be cross-referenced with table 3 and use gene descriptors. Part b does not show units or provide any information about the number of samples/replicates or what the numbers represent.
3.	Figure 6b- What do the clusters represent? Is there a color key, i.e. resveratrol gene pathways blue cluster? Do the colors from a and b correlate? More information is needed to clarify importance of the results.
4.	Figure 7- need to include N and method of detection in the description.
5.	Table 1- include a key for the abbreviations used in the table i.e., SL, DL etc.
6.	Table 2- need a reference for the method used to calculate ratio.
7.	Table 3- need a reference for the gene identity database.
8.	Table 4- the right-hand section appears to be cut off, economic what?

Grammar and English Usage
1.	Use “precision” as opposed to “precise” throughout the paper and in the title, lines 97, 98 and 358. There are probably other instances so I would recommend a search for precise in the body of the document.
2.	Line 93: Replace “The” with “A”
3.	Line 94: add “of” after tons.
4.	Line 95: annual yield of peanuts, crops, or this particular farm?
5.	Line 98: Add “the” or “a” before conventional.
6.	Line 104: are “growth” and “development” unnecessary synonyms?
7.	Line 110: Does “peanut” need to be plural?
8.	Line 137: Would replacing the comma with a colon and removing “namely” be better?
9.	Lines 174, 179, 181: The instructions switch from impersonal to first person halfway through the paragraph. This could indicate some change in how they performed the experiments, but does this need to be changed to match the whole paragraph?
10.	Line 357: “Encountered” can be removed.
11.	Line 398: Is “Accordingly” needed here or could it be cut?
12.	Lines 567-569: For this citation sources say "Journal of the Faculty of Science, Hokkaido Imperial University" is this the proper credit for Japanese publishing?
Experimental design: 1.	The abbreviation, KEGG, is mentioned several times throughout the paper including in the methods section, line 182. Include a statement on what the letters represent and the importance/significance of the pathway in evaluating results.
2.	In the results section, there are several gene families called out as significant, lines 338-339 and 345-351. Either in the table or in the body of the text include gene id# so the data can be compared. Another option would be to include the log fold difference values in the body of the text in these sections.
3. The research question is not well defined or included in the introduction.
4. The significance of the research is not tied well to previous and cited references illustrating the need for the research project.
Validity of the findings: 1.	Statistical measurements and replicates should be included on all figures and tables.
2.	Line 361: There is a statement about how robust roots are the basis of crop growth and high yields. Is there a reference or references to validate this statement? Is the case laid out for this measure in the introduction?
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: TRANSCRIPTOME ANALYSIS REVEALS THE MECHANISM OF IMPROVING ERECT-PLANT-TYPE PEANUT YIELD BY SINGLE-SEEDING PRECISION SOWING
Review round: 2
Reviewer: 1

Output:
Basic reporting: I have no question.
Experimental design: I have no question.
Validity of the findings: I have no question.
Additional comments: I have no question.


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: THE POTENTIAL FOR INCOME IMPROVEMENT AND BIODIVERSITY CONSERVATION VIA SPECIALTY COFFEE IN ETHIOPIA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The present case study gives a very detailed account of the coffee value chain in the Yayu area of Ethiopia and highlights potential income improvement and biodiversity conservation via specialty coffee. The paper is written in professional English and pleasant to read. It contributes to a better understanding of farmer decisions along the coffee value chain and possible interventions for income improvement. However, it is rather lengthy and I encourage the authors to shorten text that dilutes the focus of the paper, for instance the review of coffee certification schemes in the introduction and repetitions in the Methods section (line 294ff) and results (lines 622ff). Moreover, as an ecologist, I found the detailed description of the value chain and economic calculations quite hard to digest. Given that PeerJ has a focus on the biological and environmental sciences I would recommend shortening those parts to provide a more balanced account of economic and biodiversity issues. Perhaps some of the information could go into an appendix.
Generally, I find that the term “biodiversity” is used in a very generic way. The authors should be clearer about when they refer to forest cover (as a proxy indicator of biodiversity) and when they refer to actual biodiversity indicators such as genetic diversity, species diversity or ecosystem diversity. There is a bulk of literature from Ethiopia and other countries that shows that tropical forest degradation cannot be detected using canopy cover as the only indicator. Thus, the findings of the study with regard to biodiversity are rather preliminary.
Another concern of mine is that the manuscript does not sufficiently highlight that Ethiopia is the great exception to all coffee countries because Arabica coffee originates from Ethiopia and much of the forest coffee in southwestern Ethiopia is managed in its natural habitat. How do results from this particular case study apply to other types of coffee growing areas in Ethiopia, and worldwide, in particular with regard to biodiversity conservation?
Finally, I may add that the first author is employed by the company that purchased the specialty coffee from the case study area and I wonder if this may not create a conflict of interest.
Experimental design: The data collection method is generally well described except for a couple of shortcomings that I would like to point out. The average reader will not be familiar with the terms Forest Coffee, Semi-forest coffee and Forest Garden Coffee and thus they should be clearly defined (lines 183-184). I wonder if coffee at Yayu is really produced in Forest Coffee systems because later planted coffee (line 412) as well as farms and farm management (line 435) are mentioned. Lines 262ff: It is really hard to follow the description of the different parts of the coffee bean. How about an illustration? Is skin (pericarp) = hard coating (parchment)? Later parchment coffee is mentioned, which should be described here, too.
Fig. 1 is hard to decipher; besides, the buffer zones do not seem to be indicated in the map. An inset overview map of Ethiopia would be helpful.
Validity of the findings: The results part is very lengthy and descriptive. I wonder if some of the information could better got into the methods part, an annex, or be presented in a figure or table. The authors should take greater care to directly link the results to the three research questions; this holds true for Section 3.1 in particular.
Section 3.2 contains a mixture of results and discussion, which I would strictly separate (e.g., lines 500 ff). Furthermore, I recommend using a table or flow chart for the results rather than stating so many figures in the text which is quite a heavy read.
In Section 3.3, I have some questions about the scenarios: Is “specialty” determined each year? So could it be that in one year, the coffee scores lower and farmers will not be able to sell it as specialty coffee? Is it realistic that farmers can sell 100% of their coffee as specialty coffee, considering the logistic constraints (limited transport time)? Is the market large enough to absorb 100% specialty coffee?
Similar to the results, there is a need to double check the discussion against the three research questions stated in the beginning. I miss a more thorough discussion of whether this case study is applicable to other parts of Ethiopia, considering coffee quality, logistics and forest cover. How representative is it in terms of other coffee growing areas worldwide?
More importantly, the authors need to be more cautious regarding the links between biodiversity conservation and specialty coffee. In line 770, the term “quality of the forest” is used, but I do not think that a simple forest cover analysis can tell much about forest quality. Fig. 2 comes without any statistical test on the difference between the EVI values between the different forest types. Last but not least, the authors note themselves that the biodiversity value of forest coffee systems is not at the same level as undisturbed forest. Considering that the paper is equally about income improvement and biodiversity conservation, this warrants a more thorough discussion that should also take into account the special situation in southwestern Ethiopia. For instance, in eastern Ethiopia (Harar) coffee is grown with less shade and irrigation may be necessary.
Table 1: The conservation premium should be indicated in the table. Is this premium paid to the farmers in any case, or only for specialty coffee?
Table 2: I could not make sense of the second and third column in the table.
Additional comments: Introduction: The introduction claims that biodiversity loss and poverty are usually linked. Well, agricultural intensification and wealth can also be linked to biodiversity loss as we know from developed countries. So I would encourage the author to develop their argument in a more convincing manner, using a variety of more recent literature resources (they rely heavily on Scherr & McNeely 2007). For instance, there is a bulk of literature on the land sharing vs. land sparing topic. In line 80, “eco-agricultural (or agroecosystem) coffee production” is mentioned, but not defined. It is not clear to me if this expression refers to the special situation in southwestern Ethiopia, or to different types of global coffee production systems. In line 132, the term specialty coffee is introduced but only defined later in lines 142ff.


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: THE POTENTIAL FOR INCOME IMPROVEMENT AND BIODIVERSITY CONSERVATION VIA SPECIALTY COFFEE IN ETHIOPIA
Review round: 1
Reviewer: 2

Output:
Basic reporting: Very well written and structured. Still some small errors
Experimental design: Well researched. But some questions:
1. All cooperatives are Rainforest Alliance certified. Please explain what this means for a. coffee prices and b. other benefits to the cooperatives and its members.Please bring this also down in sections 3.3 and 4.1 to be even more clear what speciality coffee brings above vertified coffee. E.g. Utz/Rainforest Alliance certified is well known for its farmers trainings and its collaboration with TechnoServe.
2.It is not veryy clear why farmers also do side-sales to middlemen: what is the percentage ofside-sales, do they receive better prices or are they more quickly paid (457-485)? (What does this tell about the functioning of the cooperatives?) Has this been addressed in the group interviews? (Were the group interviews only with cooperative leaders or also with non-board members?)
Validity of the findings: See above.
Additional comments: Some smaller comments:
1. What do you mean with Fair Trade (99)? Utz ceritified and Rainforest Alliance were already much larger than the Fair Trade alliance before the two (Utz and Rainforest) merged.
2. 167-168: Ruben & Hoebink (2015) present ample evidence of coffee certification also in Ethiopia as well as on the functioning of coffee cooperatives in Ethiopia.


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: IT’S ALL ABOUT TIME: PRECISION AND ACCURACY OF EMOTIV EVENT-MARKING FOR ERP RESEARCH
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript presents an clear and careful investigation into the precision of several methods for sending event triggers to EEG hardware. The quality of the reporting is excellent.

The one aspect of the reporting that I wasn't very clear on was regarding the lag measures in Experiments 2 and 3, specifically to understand what was the ground-truth signal against which the triggers were compared to get the measure of lag. It is mentioned (Line 247 in methods of Exp 2) that an audio tone was generated for use by the Airmarker. Was the same tone replicated to one of the channels of the EEG system? The schematics don't show an audio input directly to the amps but I couldn't think how else the lag was determined. Table 1 mentions that lag was the difference between Emotiv and Airmarker events but, again, I wasn't exactly clear which carried the true timing signal. Is the "Emotiv event" that the authors mention mentioned the raw audio waveform from psychtoolbox?

Minor points:

Lines 86-90: The authors focus on the need for accuracy but I would have thought precision is the more important here (and is the topic of much of the paper). ERPs are the one place where you can sometimes see peaks under 5ms wide and such narrow peaks require very high precision to be correctly identified. Accuracy errors in the ERP can probably even be corrected post-hoc by looking at the ERP waveform and time-shifting it.

Line 103: Minor grammar error. "in which there exists" should be "in which there exist"

Line 209, 210: "A cut-off of activation beyond ±150 μV was set for epoch exclusion," is repeated
Experimental design: I believe the experimental design is perfectly sound and addressed the question appropriately.

I wondered whether the threshold for what was considered an acceptable jitter is appropriate. The authors used the point "at which jitter level the regression-line 95% confidence interval diverged from the zero-jitter 95% confidence interval." This seems an extreme statistical threshold. For comparing a variable value against a fixed value (a one-sample test) it's normal to compare against 95% CI but, in this instance, both values are variable and requiring the 95% CI on both is setting a very high threshold for what one considers a significant change, rather higher than a standard t-test for instance. In fact, I suspect a Bayesian test would be more appropriate since it doesn't seem appropriate this instance to stack the test in favour of the Null Hypoth as is being done here. Both aspects will likely reduce the level of jitter required to conclude that the values differ, although I'm sure it won't alter the *pattern* of the results described but it might make a difference to whether later measures fall within this binary threshold.
Validity of the findings: The findings seem appropriate and are reported clearly and without exaggeration.

The lags that have been measured are quite substantial, and seemingly come from a mixture of the Airmaker and the Emotiv system, but the precision is still reasonably high (given a 256 Hz sample rate) and that is the more important value of the two.
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: IT’S ALL ABOUT TIME: PRECISION AND ACCURACY OF EMOTIV EVENT-MARKING FOR ERP RESEARCH
Review round: 1
Reviewer: 2

Output:
Basic reporting: This article is well written and clear. For example, the explanations of core concepts are explicit and concise (e.g. definition and differentiation of ‘trigger’ and ‘event as well as ‘precision’ and ‘accuracy’.). I have only 2 main comments and remaining very minor suggestions for where reporting (including figures) could be clearer.

Main comments:
-	Line 263-266: This was the only area I had I re-read the definition a few times. I interpreted inter-trial-interval as the intervals within trigger type (i.e. interval from one Airmarker trigger to the next Airmarker trigger OR from one parallel-port trigger to the next parallel-port trigger). But line 263 confused me slightly, I think becasue the second sentence sounds as though it refers to the previous one, when I _think_ they are different things  “We then calculated the time between each of the parallel-port and Airmarker events. The variability of these inter-trial intervals (i.e., standard deviation) represented our measure of precision (or jitter). “  I think it would help if the “inter-trial-interval/precision” and "Accuracy" was marked explicitly in Figure 3.
-	Because of my misunderstanding above, I was slightly confused why the Airmarker data is not shown in Figure 4 or Table 1. For example, for Experiment 2, only the parallel port trigger data is shown in Figure 4 and Table 1, whilst the Airmarker is described in the text (line 270). It is possible that clarifying point 1 will resolve this confusion, but my initial view is that including the Airmarker data in these figs/tables would be interesting/helpful.

Minor comments:
-	Line 166: perhaps provide a citation for the ‘pre-existing, exemplary’ dataset (Badcock et al., 2013) on initial mention.
-	Line 190 – should there be a hyphen in 175-ms here or a space?
-	Line 208 – how many sampling points were used from within the normal distribution? (i.e. how many levels of jitter)
-	Line 209/210 – “A cut-off of activation beyond ±150 μV was set for epoch exclusion” is repeated twice – one can be removed.
-	Why were no epochs excluded for the highest jitter level? I am assuming due to noise but maybe be explicit.
-	Line 212 – it would be useful to refer to the exact supplemental file on OSF used for this automated peak detection. (as a side note, I commend the authors on their use of OSF to share their materials so clearly, a minor suggestion could be to add a README doc to the OSF page to allow readers to clearly navigate the materials)
-	Figure 1 – In general this figure is very informative and thorough, but a couple of small points might help clarity.
o	It would be useful to make clearer that the jitter legend corresponds to subpanel b rather than a (maybe by moving to upper right instead of top centre?).
o	The shaded area around the regression line in panel a is very subtle and tricky to spot without zooming in – could the opacity of the shaded area be increased or coloured?
-	Table 1 –  please state in legend what the asterisks correspond to and what a negative lag equates to (it might also be standard to include definition of SD acronym?)
-	Figure 5: This is a very very minor point, but it would be useful to have this larger – so a 2x2 rather that 1x4 layout could be helpful.
-	Line 355 “Results of the Flex” – missing ‘the’ at start of sentence
Experimental design: The experimental design and research questions are clear and fall within the aims and scope of this journal. I have no further comment.
Validity of the findings: The data are provided and the statistical analyses are well justified. I have two main comments, one with regards to explanation of statistical results and the second regarding the discussion:

Line 350 “This indicated that there was no difference in jitter 351 between Arduino, parallel-port, and serial-port triggering” I am not sure we can go beyond stating the difference ‘failed to reach significance’ without some support for the null (e.g. a Bayesian analysis), so for now I would recommend stating the difference ‘did not reach significance’ rather than ‘no difference’.

There are some aspects I would have liked to see expanded upon a bit more in the discussion. For example:
-	Experiment 1 uses a dataset from a single individual. Could the authors comment on whether they would expect variability in jitter thresholds across individuals? For example individuals with smaller, or noisier, original waveforms. On line 381 it is stated “large peaks in an ERPs are more resilient to jitter attenuation than are the smaller peaks.” Could this mean that individuals with smaller peaks (or paradigms producing less reliable or smaller peaks) would present more of an issue with jitter? If so I think this could be outlined in the discussion as it will be an important consideration for future researchers.
-	Because of the point above, there are some places where I wonder if this comment ‘All Emotiv event-marking configurations we tested were suitably precise for ERP research’ needs an extension to mention that the degree of jitter may depend on the ERP being investigated.
-	Importantly, the authors recommend that researchers test their respective setups to be sure of jitter with their own combination of hardware etc. Could the provided scripts be used for this? If so I think that this could be explicitly stated on line 393, as this is a further useful contribution of this work.
-	On a pragmatic note, if all systems are suitable for ERP research from a jitter perspective, could the authors briefly comment what else we (researchers) could consider when picking a method? For example, because the Airmarker is a custom built system, (which presumably is not commercially available?) engineering expertise might still be required to set up the system for ERPs in other labs? But, is it possible this system is easier to engineer than other systems? This is more a point of curiosity.
Additional comments: In this article, the authors assess the precision and accuracy of ERP event marking systems for commercially available EEG (Emotiv). In Experiment 1, they assess the sensitivity of ERPs to jitter in an existing Emotiv dataset, and derive the 'jitter threshold' for a set of ERPs (how much jitter is needed before the ERP waveform is significantly degraded). In Experiment 2 they compare the 'Airmarker' event marking system with a parallel port triggers in a research grade EEG set-up in order to assess the presence of 'lag' (accuracy) and compare the variability of inter-trial-intervals (precision). In experiment 3, the inter-trial-interval of 3 event marking systems are tested with Emotiv to assess precision in each system and 'accuracy' relative to the Airmarker system. In general the jitter of the event marking systems all fell below the jitter thresholds observed in Experiment 1. Therefore the authors conclude that these event marking systems were precise enough for ERP research.

I enjoyed reading this manuscript and I believe it will be a highly useful article for those interested in using Emotiv in their research in the future. The experimental approaches appear valid and clear. My comments therefore mainly relate to minor points on phrasing and clarification.


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: IT’S ALL ABOUT TIME: PRECISION AND ACCURACY OF EMOTIV EVENT-MARKING FOR ERP RESEARCH
Review round: 2
Reviewer: 1

Output:
Basic reporting: The quality of reporting was already very high and the authors have improved clarity on the key parts that had been less clear in the first iteration.
Experimental design: This was very strong in both iterations of the manuscript.
Validity of the findings: This was very strong in both iterations of the manuscript.
Additional comments: The paper describes a very useful set of measurements, and describes them very clearly.


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: IT’S ALL ABOUT TIME: PRECISION AND ACCURACY OF EMOTIV EVENT-MARKING FOR ERP RESEARCH
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors have addressed my previous queries regarding basic reporting. The manuscript reads clearly.
Experimental design: I previously raised no further comment on the experimental design of this study as I found this clear and well defined.
Validity of the findings: I appreciate that the authors have adjusted their phrasing of effects that failed to reach significance, and that further comment has been added to whether this would generalise to other datasets, from more than one individual.
Additional comments: I thank the authors for their revisions, they have fully addressed my concerns and I recommend publication.


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

Input:
Title: EFFECT OF VITAMIN D SUPPLEMENTATION IN PATIENTS WITH CHRONIC HEPATITIS C AFTER DIRECT-ACTING ANTIVIRAL TREATMENT: A RANDOMIZED, DOUBLE-BLIND, PLACEBO-CONTROLLED TRIAL
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: As comments below
Validity of the findings: As comments below
Additional comments: This study aimed to evaluate the effect of VitD supplementation on hepatic fibrosis in CHC after curative treatment with DAA. The surrogate markers in this study were fibrogenic and fibrolytic markers.  This study is interesting but showed negative outcomes; however need to address the followings:
	1.	Due to patients with chronic liver disease including cirrhosis, 25 hydroxylage is defected and can not converse to active form (1,25(OH)2D). Is it qualify to measure 25(OH)D level. This is acceptable for general population but not in chronic liver disease or cirrhotic patients.
	2.	In healthy population, 25(OH)D at 24 ng/ml is accepted to be adequate except high risk subjects for osteoporosis or fracture. Why this study recruited patients who vitD level 30 ng/ml.?
	3.	VitD level at 6 wk after replacement and measure only 1 time can not reflect the results (hepatic fibrosis), how the author conclude that VitD supplement is not effective.
	4.	The author did not mention for baseline markers. Theses were normal or not? If in normal range at baseline, it can explain the negative results in this study. For example when compare the baseline markers (TGFB1, TIMP-1, MMP-3 levels) with previous author study in 2017, were very high in curative treatment with DAA.
	5.	This study measured only markers without liver biopsy findings, the conclusion in the study is beyond the current finding.
	6.	The classification of vitamin D status in Table was incorrect.
	7.	Table 4,5 and figure 2&3 repeated with previous table.
	8.	How about the effect of supplementation in VitD level <10 group?


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: EFFECT OF VITAMIN D SUPPLEMENTATION IN PATIENTS WITH CHRONIC HEPATITIS C AFTER DIRECT-ACTING ANTIVIRAL TREATMENT: A RANDOMIZED, DOUBLE-BLIND, PLACEBO-CONTROLLED TRIAL
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: 1.	It is not clear to me whether the sample size was determined. The assumption was that VD may facilitate further fibrosis  amelioration which is regulated by 2 activities: fibrogenic (TGF-β1, TIMP-1) and fibrolytic (MMP-9, P3NP).  But the authors calculated sample size only based on the mean changes in serum TGF-β1 level for fibrogenic. Furthermore, there was subgroup analysis according to VD level. If so, these issues should be considered in assumption to calculate sample size for this study.
2.	The reduced liver function, not decompensated liver cirrhosis, can impact on the hydroxylation of VD into 25(OH)VD. The authors need to concern this issue in excusive criteria.
3.	Please clarify sensitiviy and specitivity of biomarker tests for liver fibrogenesis and fibrolytic.
4.	The rationale for choosing  the time intervention 6 weeks is not clear. This is only the required time for supplement VD, not for immunological change of fibrosis.
Validity of the findings: 1.   Table 5 should be reformed with accurate p-value, not only all p-value >0.05.
2.   I consider that the conclusion, "VD supplementation in CHC patients after DAA treatment does not play an important role in hepatic fibrosis regression… " is not supported by the data. The enough time for evaluating immunological change of fibrosis should be assessed before the authors could reach that conclusion.
Additional comments: This study attempts to address a clinically important issue, but I am not quite convinced that the authors have really addressed their aims. The method is described with insufficient detail and information to replicate.


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: EFFECT OF VITAMIN D SUPPLEMENTATION IN PATIENTS WITH CHRONIC HEPATITIS C AFTER DIRECT-ACTING ANTIVIRAL TREATMENT: A RANDOMIZED, DOUBLE-BLIND, PLACEBO-CONTROLLED TRIAL
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: 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: EFFECT OF VITAMIN D SUPPLEMENTATION IN PATIENTS WITH CHRONIC HEPATITIS C AFTER DIRECT-ACTING ANTIVIRAL TREATMENT: A RANDOMIZED, DOUBLE-BLIND, PLACEBO-CONTROLLED TRIAL
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: All comments addressed sufficiently. No more questions.


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: INCOMPLETE LINEAGE SORTING AND ANCIENT ADMIXTURE, AND SPECIATION WITHOUT MORPHOLOGICAL CHANGE IN GHOST-WORM CRYPTIC SPECIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript represents one of the fist comprehensive studies of gene flow between cryptic taxa in a species complex of marine microscopic animals. Meiofauna is one of the groups of animals where DNA sequences are often used to delimit taxonomic units, and this study goes a step further in attempting to understand the level and timing of gene flow to explain morphological similarity. The analyses are appropriate and provide supported results for the inference. I wish that such approach could become the standard in meiofauna and I congratulate the authors for their work.
Experimental design: The experimental design is fine
Validity of the findings: the findings are highly novel and relevant.
Additional comments: I have a series of comments to improve the strength of the message, removing weaknesses or ambiguities. These may be just subjective opinions, but consider that also other readers may have the same doubts.

1. What I do not find completely convincing is the connection between past gene flow and morphological similarity in cryptic species. The fact that gene flow exists does not explain the reason for morphological similarity. There are several examples among plants and animals, even meiofauna, where extensive gene flow and hybridisation do not preclude the possibility to identify species morphologically. This part of the rationale should be rephrased to provide convincing statements, or should be removed. I would opt for its removal, given that it does not provide more interest to the results and it only makes the rationale less convincing.

2. Another part of the rationale that is not supported is in the first paragraph of the discussion (and in parts of the introduction), where the search for the reason for the morphological similarity is not due to bottlenecks or recent admixture, and thus it is stated to be “in line with an incomplete lineage sorting scenario”. The ILS scenario is thus supported in the absence of the other causes, omitting other potential explanations. The presence of ILS is not even demonstrated, because it seems that hybridisation could be the reason for gene sharing. Thus, if hybridization exists, no ILS can be supported. Maybe a test to support whether ILS or hybridization is present should be included. Something along the line of the statistical rationale used by Joly et al (https://www.journals.uchicago.edu/doi/full/10.1086/600082) may do the job. In any case, even after such test, the connection with morphological similarity is weak. Only a comparison with the level of gene flow between closely related species groups of taxa that are morphologically distinguishable and diverging at the same time could be used to identify the reason for morphological similarity in cryptic taxa.

3. Overall, the idea is great, the data and the analyses surely worth, but the rationale to fit the results in the idea of searching for a reason for morphological similarity weak, and not necessary.

Other issues
4. The idea of cryptic species being taxonomic artefacts is reported in the abstract and in the introduction without any further explanation. My suggestion is to (i) expand the idea and clearly explain it in the introduction, given that most readers will disagree on it, and to (ii) remove it from the abstract, where it may represent an ambiguous weakness for several readers.

5. Also the idea that cryptic species are overlooked, on line 46, is not unambiguous. If anything, most taxonomic studies nowadays deal with DNA sequences and make integrative taxonomy the rule and not the exception. I understand that this is only my subjective opinion, based on the organisms I work with; yet, there is no reason to upset some readers with unsupported statements and I would suggest to remove the phrase ‘yet overlooked’ on line 46.

6. The nomenclature of the species complex is not always clear. For example, on line 89, it is reported as “The Stygocapitella species cryptic complex”, which does not make much sense, because (i) it does not report the name of the species complex but only of the genus, and (ii) the order “species cryptic complex” is not understandable. The same problem of unclear nomenclature appears already in the title and in the abstract: a complex of cryptic species cannot be identified by the name of a genus. One genus may contain several easily distinguishable species and also several species complexes, which are all named individually usually by using the name of one of the species in the complex. The problem is clearly seen in the sentence on line 89, where 11 species with 4 morphotypes are mentioned, revealing that not only one, but 4 complexes of cryptic species, which cannot be distinguished using morphology alone, exist in the genus. Please, remove this ambiguity in the terminology and clarify what the complexes are.

7. The hypotheses at the end of the introduction are unclear and unsupported. H1 bottlenecks and founder effects should not only provide morphological similarity; bottlenecks and founder effects, by reducing genetic variability within each population of each species, maximise differences between populations and between species, which is the opposite of what is stated. It is true that bottlenecks reduce genetic variability, as stated in the discussion on line 512, but bottlenecks are one of the traditionally accepted mechanisms to have genetic diversity between populations, quickly leading to speciation, again in the opposite direction of what is assumed in the hypothesis. Think of the bottleneck and founder effects on islands, quickly leading to morphological differences between the island and the source populations. Please, clarify the rationale for this hypothesis. H2 implies that hybridisation makes species more similar, but there are lots of examples of complexes of hybridising species that can still be distinguished morphologically, for example in plants but also in other microscopic aanimals where evidence of mitonuclear discordance has been found. H3 could be OK, but the fact that ILS is present should be clearly tested and not assumed.

8. On line 86-87, the sentence “Very few biogeographic and systematic studies, let alone evolutionary studies, have thus contributed to the discussion” is then followed by a list of 6 references (several from the authors), making the sentence not so supported. A list of 6 references cannot be considered to represent “very few” studies, considering that several other studies have not been mentioned. Especially in meiofauna, the use of DNA taxonomy in the study of biodiversity in all its aspects (including biogeography and evolution) has a long history and several readers may not agree on the sentence.

9. Given that the study is on species, it would be better to use zoological nomenclature according to the strictest rules in taxonomy, reporting species authorship at the first citation of a species in the main text, taking care of reporting the correct use of parentheses.

10. The chapter starting with the title on line 159 on “Species delimitation” does not describe any method of species delimitation but only the “multi-marker phylogeny”. Either change the title or include a description of the methods that are used for species delimitation.

11. In the same chapter, a sentence should state whether ITS was present with double peaks or not, and how the double peaks were treated. Check this method for double peaks in ITS in species delimitation: https://besjournals.onlinelibrary.wiley.com/doi/abs/10.1111/2041-210X.13454. I am not suggesting to use haploweb, but I only want to point out that the reader may need to know what happened to the double peaks in ITS1.

12. Line 359: ‘taxa’ does not seem to be the correct term, as the idea refers to ‘individuals’

13. The long discussion on pooling individuals for RADseq seems out of place. Please, shorten it considerably. It is already convincing that the study managed to get good genomic data from single animals through WGA. Also the caveats due to WGA should be shortened, and especially moved at the end of the discussion. It would be much better first to discuss the biological implications of the results, and then only later introduce the potential problems. Starting the discussion with problems seems to distract the reader. Just a minor point: WGA works also for rotifers, which are much smaller than the analysed anellids (https://www.sciencedirect.com/science/article/pii/S0960982216000816; https://journals.plos.org/plosbiology/article?id=10.1371/journal.pbio.2004830).

14. The discussion in the part on line 521 is weak. ILS and hybridisation can be distinguished statistically (https://www.journals.uchicago.edu/doi/full/10.1086/600082) and the manuscript remains too ambiguous on this point, stating that admixture could be due to one of the two processes, but then without testing which is more likely.

15. In the same part of the discussion, the speculation on sympatric and non sympatric populations is also weak: if the estimates are correct, gene flow can happen every thousands of years, meaning that animals from different populations have the time to move from one population to the other.

16. The selection of references is a bit too much biased towards the production of the authors. Whereas I would say that it is a good option for the discussion, having too many references from the authors in the introduction may leave the impression that only the authors care about this topic, with no broad interest. This is not true, and several studies on cryptic species, their origin, and their biogeography exist in the meiofauna, other than in anellids.

17. The choice of colours representing the three species in the figures is not the best one: two of the three species will not be clearly seen by several readers with colour vision impediments (green and orange may be mixed up). Choose a set of three easily distinguishable colours to be more inclusive.

18. The English language is rather good, but please consider a careful revision, in order to remove very minor problems such as:
-	Single comma between subject and verb (e.g. on line 42).
-	No hyphens are allowed for adverbs ending with –ly (e.g. on line 49, 61, 62, etc.); this is called a hypercorrection, because no ambiguity is possible with such adverbs and thus the hyphen is redundant. The text is already ambiguous in the use of such hyphen, because in some instances the adverbs are already reported without the hyphen (e.g. line 91).
-	Hyphens are not used consistently also in other phrases, for example “missing-data” on line 274 should not have the hyphen. Please, carefully check the use of all the hyphens in the text.
-	The term ‘specimen’ is used ambiguously: strictly speaking, ‘specimen’ is a representative individual or part of it, stored in a collection, whereas in the manuscript it is used with the meaning of a single individual. I guess that the animal is completely destroyed by the DNA extraction, and thus the ‘specimen’ is lost and cannot be considered a specimen anymore. In addition, the phrase ‘individual specimen’ is a tautology. The misleading use of ‘specimen’ is only a minor problem, but for entomologists and other readers who work in museums the manuscript will seem weird. Thus, there is nothing to gain by using ‘specimen’ instead of ‘individual’, which will make all readers happy.
-	‘a loci has’ should be ‘a locus has’.
-	‘These statistics consists’ should be ‘These statistics consist’.
-	‘which’ is used for both restrictive and non-restrictive clauses, but at least one instance of the use of ‘that’ instead of ‘which’ are present (e.g. line 485) and should be removed for consistency.
-	On line 368, ‘the least amount’ should be ‘the lowest amount’, because amount is countable.

I hope that my comments could be useful to strengthen the impact of the message of the study.
Yours sincerely,
Diego Fontaneto


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: INCOMPLETE LINEAGE SORTING AND ANCIENT ADMIXTURE, AND SPECIATION WITHOUT MORPHOLOGICAL CHANGE IN GHOST-WORM CRYPTIC SPECIES
Review round: 1
Reviewer: 2

Output:
Basic reporting: I think this is an extraordinary contribution to our understanding of the factors that determine the existence of cryptic species, and the current debate of the increasing discovery and the lack of integration into an evolutionary framework as discussed by the authors.
In my opinion the paper covers the most relevant literature published on the subject, it is very well-written and structured and all the hypothesis are very well tested and discussed. No ambiguity I can see from reading this nice piece of work  .
On lines 56-64 author present idean on how the discovery of cryptic species is important in terms of biological systematics, but also in other fields in terms of their practical impact, I would suggest to use the example of parasitic organisms, where this fact has been clearly shown at least in two studies (Pérez-Ponce de León and Nadler, 2010 Journal of Parasitology 96, 453-464, and Nadler and Pérez-Ponce de León 2011 Parasitology 138, 1688-1709. .

It is mentioned in the introduction that the genus contain 11 species, although in WoRMS (World Register of Marine Species), only 8 are reported.
Experimental design: The methodological approach to test the hypothesis that morphological similarity among three species of the polychaet Stygocapitella is the result of either bottlenecks, recent admixture or incomplete lineage sorting is sound and actually it is on the state-of-the-art since it uses whole genome data and a vast array of methods currently available.
In my opinion, the question is fully addressed and the conclusions are very clear.

I have a question regarding the use of independent molecular markers.  It is mentioned in the results section lns 286-294 that authors compiled a dataset of 4,147 bp, for 4 molecular markers (COI, 16S, ITS1, 18S), and the phylogenetic tree is the result of the concatenated analysis (Fig. 2A), although the sample size for each of them is quite variable, did the authors check for the reliability of presenting a concatenated analysis of the 4 markers?. I think that part of the methodology is very short and not fully explained.
Validity of the findings: The approach followed by this paper is novel, and points to the use of genome data to fully understand the factors that determine the occurrence of cryptic species in natural systems, including the 11 potential causes outlined by authors on lns 71-82 of this paper.
In my opinion, conclusions are clear and open a clear path to demonstrate with other empirical studies that the processes underlying the morphological similarity among the 3 species of Stygocapitella studied in this work.  The analyses left some room for speculation, which in my opinion is well justified.
Additional comments: Very nice piece of work!.


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

Input:
Title: INCOMPLETE LINEAGE SORTING AND ANCIENT ADMIXTURE, AND SPECIATION WITHOUT MORPHOLOGICAL CHANGE IN GHOST-WORM CRYPTIC SPECIES
Review round: 1
Reviewer: 3

Output:
Basic reporting: In this contribution, Cerca et al study the population genetics of 3 cryptic and partially sympatric species of the meiofaunal worm Stygocapitella. Based on previous work with a limited number of markers, the 3 lineages were recognized and here they evaluate whether the morphological similarity is a result of recent bottlenecks, continuous gene flow or incomplete lineage sorting. The paper is well-written and figures are informative. The DNA data deposition statement includes raw Illumina reads but not Sanger sequences (maybe it could mention they are in supp table 2 for easy access?). Code is not provided in the current version, which prevented interpretation of some results (see Experimental design)

Given the general lack of knowledge on the diversification of meiofauna and the huge diversity of these animals, this paper is a relevant advance showing how speciation does not necessarily lead to morphological differentiation, and attempting to rule out some of the hypotheses explaining that. The extensive geographical sampling and transparency in presentation of results are also noteworthy. Another important outcome of the study is the presentation of a methodology to work with challenging samples represented by these small animals: some of the reasons for the lack of studies are precisely the difficulty in sampling and applying standard molecular protocols to these organisms.

I believe, however, that some of the results presented in the paper could be artifactual, and more work could be done to demonstrate their validity before publishing. Specifically, despite the efforts to mitigate these problems, missing data could still be affecting the results, the interpretation of coalescent models is problematic, and the data could be further filtered to remove artifacts arising, for example, from paralogy. I believe that rejection of hypotheses 1 and 2 (bottleneck and introgression) could be due to artifacts, and therefore more analyses are needed to demonstrate that this is not the case (or to review the conclusions, if it is). That said, I also believe that all problems can be addressed with the data available, and below I make suggestions for each point.
Experimental design: The research questions are well-defined, but I believe their framing could be improved. Specifically, the end of the introduction seems to suggest that one of the three hypotheses is the cause for cryptic species, when earlier the authors list more processes that cannot be tested with data in hand (for example, stabilizing selection on phenotypes). It is well possible that the three species have not undergone bottlenecks, do not hybridize and do not retain ancestral polymorphisms and yet are morphologically similar. Similarly, finding that ILS exists in this system does not imply that it is responsible for the morphological stasis and other, untested, processes are not occurring (such as stabilizing selection). The authors could acknowledge that more explicitly.

Methods are generally described in detail, but in several instances the authors refer important information to other papers. In some instances (specific comments in minor suggestions below), relevant information could be repeated in this paper. Below I make a few comments on the major points in which methodological choices can impact results:

The parameter files for fastsimcoal are not provided, nor any description of the parameters used. This is important, because the authors use the absolute number of generations to species divergence to rule out some of the coalescent scenarios. It is somewhat unfortunate that fastsimcoal works with absolute numbers instead of coalescent units, since inference of absolute effective population sizes and divergence times is only reliable if there are reliable mutation rates. Since the mutation rate used (and a justification for its choice) is not provided, I believe that direct interpretation of coalescent times in generations is problematic. Therefore, I find the conclusion that there is no gene flow between species unconvincing when models with gene flow are clearly well supported. Moreover, since both ancient gene flow and recent gene flow between s-w were supported, maybe it would be important to add a model with these two migration parameters simultaneously. Finally, it is not clear whether gene flows assumed to be symmetric. If it is highly asymmetric, and assumed to be symmetric, one could be missing scenarios of gene flow with very strong support from the data.

Another important fact for interpretation of results and not thoroughly discussed in text is missing data in the Sanger dataset used to evaluate species identities. It seems that for many samples the data is heavily biased to the two mitocondrial genes. The authors refer to previous work to say that there is no discordance between genes from the Sanger sequencing dataset, but it is not clear if this previous work included the few samples with discordance between datasets found here. Could it be that the labelling of species is only reflecting mitocondrial lineages? In that case, it is possible that rare introgression affecting only a small part of the genome (such as mtDNA) is driving observed patterns, at least in part. Maybe showing trees for each gene, highlighting samples placed "incorrectly" in the concatenated SNP dataset would help in understanding patterns.

Despite all the effort to minimize missing data, it seems that there might be still substantial missing data for some individuals. A table with amount of missing data per sample could help to visualize that. Fig 2A shows a typical pattern when adegenet is used in datasets with large amounts of missing data: samples with large amounts of missing data are pulled to the middle, obscuring patterns. This is because adegenet uses a very simple rule for imputing missing data: replacing these with average allele frequencies. This may be problematic in a sample with substantial missing data (close to 50%, for example), and the differences between MDS (which I assume ignores pairwise missing data) and PCA indicate that this may be a problem.
See, for example, the following reference:
Larson, WA, Isermann, DA, Feiner, ZS. Incomplete bioinformatic filtering and inadequate age and growth analysis lead to an incorrect inference of harvested‐induced changes. Evol Appl. 2020; 00: 1– 12. https://doi.org/10.1111/eva.13122
Moreover, as also discussed in the reference above, it is possible that the dataset includes problems such as paralogy, which can further obscure patterns and affect inferences. The text does not mention a filter for paralogy, for example.
To mitigate both problems, I recommend using genotype likelihoods instead of called genotypes for doing the PCA. This is implemented in PCAngsd:
Meisner J & Albrechtsen A. 2018. Inferring population structure and admixture proportions in low-depth NGS data. Genetics 210: 719–731.
The same program also provides a method for testing sites for Hardy-Weinberg equilibrium while considering population structure, which is a powerful method to remove artifacts such as paralogy:
Meisner J & Albrechtsen A. 2019. Testing for Hardy–Weinberg equilibrium in structured populations using genotype or low-depth next generation sequencing data. Mol. Ecol. Resour. 19: 1144–1152.
Implementing these would require some changes to the workflow in the paper, notably not using genotypes called by stacks but rather using stacks loci only to produce a reference "genome" onto which raw reads are mapped and then used as input to ANGSD (http://www.popgen.dk/angsd/index.php/ANGSD) followed by PCAngsd. Given the nature of the dataset, I believe it is important to use a method less sensitive to missing data. The usage of genotype likelihoods would decrease the amount of missing data by allowing lower-coverage loci, the PCA would be estimated without the bias mentioned above and problematic loci would be filtered. This might have significant consequences for results presented.

A final point that I believe deserves attention is the choice to filter SNPs with minimum allele frequency below 0.05. Given the sample sizes used here, it would be possible to detect alleles with frequencies lower than that, an I am wondering if ignoring low-frequency alleles has an effect on statistics such as Tajima's D. If this is the case, the conclusion that populations did not experience bottlenecks could also be an artifact. I would recommend testing the effects of a lower theshold, perhaps 1/N, where N is the number of samples sequenced.
Validity of the findings: The discussion is well-written. However, given the concerns raised in Experimental Design above, I believe that a careful discussion of the validity of the findings can only be done after concerns about artifacts are addressed.
Additional comments: Minor suggestions

throughout the text: species names are not italicized

line 110 - I believe "Maps" is not the last name of "Google Maps", please revise this reference
line 180 - even though a reference on best practices is cited, the authors could briefly comment on which criteria were used to select -M 3 and -n 3. Why was this considered the best combination?
line 190 - what is PeerJ policy for citing unpublished data?
line 450 - "stochastic biases" - I find this construction confusing, not sure if by this the authors mean random or systematic errors.
Supplementary Table 2 - The legend mentions that "bad apples" are defined in the main text, but no reference is made there.

Fig 2 - what is A0, A1? Are these the concatenation of the two alleles? If this is the case, since RAD loci are generally unlinked, I do not think that considering them as separate terminals makes much sense. Maybe using the consensus for each sample?
Additionally, it is not clear what "shared pairwise data" means. Is this the average number of loci shared with other samples? Why is it different for A0 and A1 for a given sample?

fig 6 - The figure is missing y axis label. Moreover, is this really likelihood, or is this AIC? I believe this may be the AIC, since one would expect the likelihood to increase with more model parameters.