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: VALIDATION AND ANALYSIS OF THE GEOGRAPHICAL ORIGIN OF ANGELICA SINENSIS (OLIV.) DIELS USING MULTI-ELEMENT AND STABLE ISOTOPES
Review round: 1
Reviewer: 1

Output:
Basic reporting: Overall, the writing of this submission needed at least another round or two of edits to meet the minimum standards of PeerJ. Throughout the manuscript there are many grammatical and spelling errors that effect the clarity of the study. Unfortunately, these are too numerous to list here but some examples:

Line 18: Background section of abstract is very confusing.
Line 58: What is the difference between “human material exchanges” and the import and export trade? Aren’t this the same thing?
Line 83: “The fingerprint of mineral elements and stable isotopes in plants is a unique "brand" in environments.”
Line 106: “semi-humid-mid-temperate semi-arid” too many hyphens
Line 358: “most studies have shown that the mineral elements in the soil are significantly related to their mineral elements “
Lines 369 and 372: “the relative size of CO2 in the external environment and the CO2 concentration between plant cells” and “The size of stable oxygen isotopes in plants”. I believe the author is referring to the δ13C and δ18O values?

Many of the grammatical issues could be fixed with some minor revisions, however, the structure of the paper deeply flawed. The manuscript’s introduction doesn’t do a good job establishing relevant background for the study nor does it provide the reader with reason to be invested in the research. It is not clear to me why the provenance of A.sinensis in the Gansu Province is important. The first two paragraphs of the Introduction try to establish this importance but provide only tangential information. While it is important to put A.sinensis in a cultural and economic context, these two paragraphs could probably have been cut to ¼ in length. In fact, the discussion does a significantly better job at establishing relevant background for this study. For example:

Line 319-351: These paragraphs read more as “Introduction” and should be moved to that section. Much of this section is establishing other studies of “food provenance”. However, I think some of these examples that do not involve stable isotopes or mineral elements could be viewed as tangential and could be excised.

Line 356-385: Much of these sections could be condensed and moved to the Introduction
Additionally, a section of the discussion (Lines 390-423) could be condensed and moved to the methods under “Statistical Analysis” as it justifies the statistical tools used in this manuscript. Unfortunately this leaves very little for the discussion itself which would then need to be further fleshed out.

The statistical results take up a significant part of the manuscript. This likely could be more concise.

The figures and tables have several formatting problems:

Figure 1: The legend shouldn’t be intersected by the Latitude and Longitude. The font of all the text is too small to read. The font should be 12pt. The scales for provincial and regional maps are too small. The provincial map shouldn’t have Latitude and Longitude lines or its own tiny legend. It is also too small to have the regions of the Gansu province named in the smaller map. Names of regions should be indicated in all the areas of the larger map. Large arrow should not be necessary with adequate Figure description.

Figure 2: The font of all the text is too small to read. The font should be 12pt. All sections of the figure could be put into their own boxes to make it a bit clearer. Some of the text seems scrunched like the text at the far right of 2B.

Figure 3: The font of all the text is too small to read. The Legend is too small. The individual datapoints are difficult to differentiate and should be larger. The “group centroid” datapoint should also be included in the legend.

Figure 4: The font of all the text is too small to read. The Legend is too small. Axes could be thicker to increase clarity. Subfigure letters should probably be of a consistent size across figures.

Figure 5: The font of all the text is too small to read. The Legend is too small. Axes lines and error lines could be thicker. The shading on the bars should be removed. It appears that this figure has been compressed vertically.

Figure 6: The font of all the text is too small to read. The whole figure appears fuzzy. It is not at the proper DPI. Sample icons should be the same across all figures. The colors are the same for each region across figures but Figures 1 and 3 use different shapes while Figures 4 and 6 only use circules.

Table 1: The font of all the text is too small to read. “n” is unnecessary in the table given that all variables are n = 25. Min/max and range should be combined into one line (e.g., for K: 2806.75 – 8234.19). Multiple metrics of variation included here seem unnecessary. This table can be pared down to only essential elements for the results and discussion.

Table 2: No description of what “a” and “b” superscript mean in the description of table. Type of statistical analyses should be Table description and not a note.

Table 3: Lots of empty space. Could this be redesigned to be smaller.

Table 5: Provenance is spelled wrong. There isn’t a need to capitalize the letters in the middle of the region names.

Table6: Same as Table 5
Experimental design: The primary research within this manuscript does fall within the aims and scope of PeerJ. The authors are relatively clear that this study provide geochemical tools to determine provenance of A.sinensis. However, they do not fully establish why this information is important.

I’ve touched up on “Statistical analysis” subsection of the methods previously and the “Study area and sample collection” provides adequate information. The “mineral elements analysis” subsection also appears to provide a good concise description. However, there are major concerns with the “Stable isotope measurement” subsection:

Line 119-122: I believe the authors are trying to say they are using the δ13CVPDB, δ15NAir and δ18OV-SMOW scales for their stable isotope analyses. The way that it is written implies they used VPDB, Air and SMOW as standards within their stable isotope analyses.

Line 123: “wheat flour δ13C (δ13CVPDB=-13.68±0.2 (‰)) and δ15N (δ15NAir=1.58±0.15 (‰))” These are the same values stated earlier for the international scale. We are not given the value of their internal wheat standard nor its origin. Is it a standard verified by USGS or IAEA? An internal standard calibrated with verified stable isotope standards?

Line 124: The authors are only using a single standard for their stable isotope analyses. It is recommended to use at the minimum two stable isotope standards with values representing the range of expected values within analyses. I would be wary to trust this data completely. Furthermore, there likely should have been a standard weighed at different masses to correct for amplitude and one or more standards for independent checks. The authors also do not indicate if there were any replicates in the analyses.

Line 126: The author does not provide what standard or standards they used for δ18O analyses.

Line 128: The author does not provide the target weights for their carbon and nitrogen stable isotope analyses.

Line 131-132: It is not mentioned that samples for δ18O analyses should be placed silver cups. The authors also do not provide the peripheral that was used for the analyses, only the IRMS. TC/EA? FlashEA?

Line 132-138: Description on how delta values are calculated is unnecessary.
I am also curious as to why the authors did not generate data for δ34S or δ2H. Both are used in other food provenance studies (e.g., Camin et al 2017). While sulfur has its complications and the author’s FlashEA might not be set up for sulfur, δ2H is typically measured simultaneous with δ18O. The additional isotopes could have provided a much more robust analysis.
Validity of the findings: While modelling is not field of expertise, the statistical analyses and the results presented in this manuscript appear relatively sound and follow what has been established in earlier provenance studies. However, I would like to reiterate that the results section is hard to follow and need significant streamlining to brevity and clarity.

The authors did include their data but it lacks GPS coordinates for each sample and having the values for the standards would provide us more confidence in the data.

Any misgivings I’d have for the validity of the findings are related in the lack of robustness in the stable isotope analyses. From the methods it is hard for me to determine if the authors have a firm grasp of the process of stable isotope analysis. This is not helped by the lack of information and the misinformation in that section of the methods. I would have preferred to see additional use of isotopic standards from carbon and nitrogen along with perhaps the inclusion of hydrogen and sulfur if feasible. This being said, the authors were able to effectively model the provenance of A.sinensis using just 25 individuals across the 3 regions.

The final conclusions for the manuscript are succinct and effectively summarize the results but don’t tie in very well to introduction or the broader impact. Again, from the manuscript, it is difficult to know why the provenance of A.sinensis is important economically, culturally or medically.
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: VALIDATION AND ANALYSIS OF THE GEOGRAPHICAL ORIGIN OF ANGELICA SINENSIS (OLIV.) DIELS USING MULTI-ELEMENT AND STABLE ISOTOPES
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is written in clear language, having a logical path for information from introduction, methods and results collection. Nonetheless, for the first part of the discussion paragraph, it is advisable to be moved under introduction as they refer to other studies on geographical traceability which usually it should be under the introductory or bibliography part of the manuscript.
Under “discussion” it should be limited to make comparison of collected data from previous studies

Such study is mainly based on the application of statistical analysis as tool to extract evidence for traceability, thus it is highly recommended to explain the objective of each tool used to extract data in the paragraph of “Statistical Analysis”, as the use of some of those tools was not very clear in interpretation of relationship between different variables, besides that many tools were used along the whole study

The listed references are relevant to the topic and considered between state of the art references for geographical traceability; besides that most references dated from less than 10 years

All presented figures, tables together with their labeling are very well clear and most data are reflected in the discussion part.
Experimental design: The study was designed in structured way; collecting samples from 3 regions as origin of the plant Angelica Sinensis. Knowing that number of samples should be higher as 7 samples from one area could not be enough to reflect the representativity of the soil type which has an impact on tracing the origin of samples.
Validity of the findings: data reported in this study matches previous studies in term of statistical analysis tool and interpretation,

Regarding analytical methods, the author used traditional methods applicable to such type of study based on stable isotopes and total concentration of selected elements.

The missing part is quality control data for total element analysis, as it should be part from evaluation of credibility of data
Additional comments: Few notes are to mention and to be considered by author

- Page 8 line 120: please check the values of CRM Vienna pee Dee belemnite (δ13CVPDB=-13.68‰),Air (δ15NAir=1.58‰) and Vienna
-	line 148: usually during acid digestion we need to take good care not to loose any volatile elements… so lid should stay closed till the sample get to the ambient temperature
-	line 159; the author mentioned “A small number of LOQ…” ; it is not clear why they decided to devide by square root of 2? What does it mean “A small number…” how many ?? why not all ?? it needs to elaborate more on this sentence
-	LoQ for stable isotopes? Can the author elaborate how to compute this parameters for stable isotopes???
-	Line 179: do the stable isotopes values reported are the average of all samples from each region??
-	Line 180: the values of coefficient of variation is related to the variation within the samples from each region or from the 3 regions??
-	Line 178 the author mentioned already that variation of Al and Cr are high; again in line 181 same idea is repeated but including δ15N; so it is better to rearrange the results 1- per values level, 2- per variability within the group
-	What the author meant by presenting the ration between only selected elements Zn/Mn, Cu/Cr… while not for others as it was not reflected in the text and the objectives from this ratio
-	The variation δ13C of is usually not related to the level of precipitation while it is applicable for O18 and Deuterium
-	Line 360-363 it needs rewording , very complicated sentence
-	Table 2 labelling: what the author meant “with statistical analysis data … although the values reported are the concentration of total elemnts and Delta values for N, O and C


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: VALIDATION AND ANALYSIS OF THE GEOGRAPHICAL ORIGIN OF ANGELICA SINENSIS (OLIV.) DIELS USING MULTI-ELEMENT AND STABLE ISOTOPES
Review round: 2
Reviewer: 1

Output:
Basic reporting: The manuscript as a whole is greatly improved from the first draft submitted. There are still a number of issues with spelling and grammar but these are minor compared to the structural issues in the original submission. I've provided some examples below but these are far from exhaustive. There needs to be another serious pass here on grammar and spelling.

Line 53: Maybe say “effective scientific tools and techniques”?
Line 61: provenance is a good term in place of “source authenticity”
Line 61-63: I understand what you are trying to say here but it might not be clear to all readers. I assume you mean that the phylogeography can provide interrelatedness among natural populations but not necessarily the geographic origin of cultivated plants?
Line 64: remove trace of
Line 78: components instead of ingredients
Line 79: tool instead of target
Line 80: “Stable isotopes of plants” instead of stable plant isotopes
Line 82: d13C values instead of “stable carbon isotope”. You can also use “stable
carbon isotope values”
Line 83-84: A bit hard to follow. Do you mean the pCO2 between the external environment and within the plant leaf/mesophyll? I understand what you are trying to say again but it could use more clarity.
Line 85 you can probably drop the sentence “When the interceullar…”
Line 88-89: You can mention isoscapes also?

Line 123: awkward sentence. “We weighed 5.0 mg of homogenized/ground A sinensis into tin capsules” or something similar would read better.

Line 127: “To bring our samples to international stable isotope values…etc” instead of “Use USGS24…”

Line 129 and 139: You can probably drop the sentences with VSMOW and VPDB

Line 130: “long term accuracy/precision” of instrument instead of long term standard deviation for d13C

Line 131: B2159 is a Sorghum Flour std from Elemental Microanalysis I believe. It’s d15N value here is reported correctly but d13C should be -13.78 based on the most recent certificate. (However I understand that you may have a different batch than what is presently available for purchase. You may want to report the batch number and that the standard is from Elemental Microanalysis.

Line 133: The internal B2159 standard doesn’t prevent drift but allows you to drift correct your sample runs.

Line 378-383: This paragraph would fit better in the intro as a justification of using trace elements and stable isotope data.

Lines 384-403: Paragraph need to be tightened up and better tied into the study as a whole.

Figure 1: Move the legend so nothing overlaps with the letters

Figure 2: ABCD are too large. Reduce font size and ensure they don't overlap with the lines between panels.

Figure 3: A and B could be smaller fonts
Experimental design: Overall the authors adequately responded to my critiques.Some structural and accuracy issues are touched upon in "Basic reporting".
Validity of the findings: The authors overall were able to incorporate my critiques into the manuscript in an acceptable fashion.
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: ESTABLISHMENT OF A FERROPTOSIS-RELATED GENE SIGNATURE FOR PROGNOSIS IN LUNG ADENOCARCINOMA PATIENTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The title, abstract, introduction, methods, results and discussion are appropriate for the content of the text. Furthermore, the article is well constructed, the experiments are well conducted, and analysis is well performed. The figures are relevant, high quality, well labelled and described.
Experimental design: The experimental design is original and the research is within the scope of the journal.. Research question is well defined, relevant and meaningful. The methods are highly technical, ethical and logistical. Statistical methods are chosen correctly.
Validity of the findings: All underlying data have been provided in detail. The findings are meaningful. The conclusions are well stated and relevant to the research questions.
Additional comments: This paper investigates the function of expression of ferroptosis-related genes in  overall survival(OS) and prognosis of lung adenocarcinoma(LUAD) by analyzing TCGA datasets. The authors identified a ferroptosis-related gene signature by univariate Cox regression analysis. Moreover, the authors validate their findings in a GEO dataset. To explore further about the related pathways, the authors demonstrate that risk score was prominently enriched in ferroptosis processes. In short, this study identified the ferroptosis-related gene signature as a potential predictor for the prognosis of LUAD.

Editorial Criteria
BASIC REPORTING
The title, abstract, introduction, methods, results and discussion are appropriate for the content of the text. Furthermore, the article is well constructed, the experiments are well conducted, and analysis is well performed. The figures are relevant, high quality, well labelled and described.
EXPERIMENTAL DESIGN
The experimental design is original and the research is within the scope of the journal.. Research question is well defined, relevant and meaningful. The methods are highly technical, ethical and logistical. Statistical methods are chosen correctly.
VALIDITY OF THE FINDINGS
All underlying data have been provided in detail. The findings are meaningful. The conclusions are well stated and relevant to the research questions.

Overall, I think this paper is novel and will be of interest to the community of lung cancer genetics, especially LUAD research. The statistical part is valid and makes sense. The authors make it comprehensive by integrating analysis of multiple sources including GEO and TCGA. The main strengths of this paper is that it addresses an interesting and unexplored question, finds a novel discovery based on a carefully selected set of bioinformatic procedures. As such this article represents an excellent and elegant bioinformatics study which will almost certainly influence our thinking about the function of ferroptosis-related genes in LUAD. Some of the weaknesses are the lack of in vitro or in vivo validation experiments. In general, the work is convincing except some major and minor comments below:

Major Comments:

The Methods of the Abstract are too simple, I would recommend expanding it and adding details like what datasets were used, what statistical methods were used to construct the prediction model, what pathway analysis methods were used. Some contents in the Results could be moved to the Methods.

I do see multiple platforms and normalization methods for LUAD samples in GDC, which includes HTSeq - Counts (sample size: 594), HTSeq - FPKM(sample size: 594) and HTSeq - FPKM-UQ(sample size: 594). Please explain why the sample size in the manuscript is 528 rather than 594. Please also explain why “HTSeq - FPKM” was chosen for analysis, rather than the other two platforms?

I’m wondering if there are any ongoing clinical trials focusing on ferroptosis-related genes identified in this study in LUAD or other types of lung cancer? It will be very strong evidence for the significance of the current study if so.

I’m just wondering if the differences in sequencing platforms affects the results, since the discovery dataset(TCGA) is RNA-seq, and the validation dataset(GEO) is microarray (GPL96 Affymetrix GeneChip Human Genome). I’m wondering if a RNA-seq LUAD dataset as a validation dataset will produce more significant results.

Minor Comments:
Line 58: please replace “UCSC Xena browser (https://xena.ucsc.edu/)” with “NCI Genomic Data Commons (https://portal.gdc.cancer.gov)”. Since GDC is the official data host for TCGA data. Please also add this paper as reference for GDC: https://www.nature.com/articles/s41588-021-00791-5 .

It is great that a session of abbreviations was there to list all the abbreviations for the database names. I would also recommend including abbreviations like LUAD, TCGA, GEO, DEG, GO, KEGG etc in that list.

All the gene names should be italic for all the gene names.

Line 37: please remove the “- -” in the beginning.


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: ESTABLISHMENT OF A FERROPTOSIS-RELATED GENE SIGNATURE FOR PROGNOSIS IN LUNG ADENOCARCINOMA PATIENTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The language used is clear and unambiguous, but introduction and discussion need to be revised by citing the most relevant and recent studies focusing on the correlation between ferroptosis and cancer. For example, cancer cells bearing the mesenchymal phenotype, as well as drug tolerant cancer cells, may be vulnerable to ferroptosis induction ( doi: 10.1038/nature23007, doi: 10.1038/nature24297) and oncogenes can interact with the ferroptotic pathway, rewiring the tumor cells by regulating the expression of the main components of ferroptosis (doi: 10.1158/0008-5472.CAN-20-1641).

Figures 2B, 2C, 3, 5 and 7 are extremely small and their size/resolution has to be improved in order for the specific data to become visible.
Experimental design: The research was within Aims and Scope of the journal and rigorous investigation performed to a high technical & ethical standard.
Validity of the findings: No comments.
Additional comments: In this manuscript Cai et al. elucidate the association between ferroptosis-related genes and prognosis in patients with LUAD (Lung Adenocarcinoma). Specifically, 74 genes involved in ferroptosis mechanisms were found to be differentially expressed between tumor and adjacent normal tissues after interrogating the TCGA and the FerrDb database. A five-gene signature was constructed using multivariate Cox proportional analysis and signature-based risk scores were used to classify patients as high and low risk. Kaplan-Meier survival curves confirmed that Overall Survival was significantly worse in high-risk compared with low-risk patients. Additionally, by performing gene set enrichment analysis and interrogating biochemical pathway databases the authors conclude that the differential expressed genes were mostly enriched in the ferroptosis and the immune-related pathways. In the current study the authors attempt to address an important question by identifying a prognostic marker for lung adenocarcinoma. My specific comments are listed below.

Even though the study is well constructed it lacks novelty, since ferroptosis-related genes have recently been investigated as prognosis prediction markers for lung adenocarcinoma by a recent study by Gao X. et al, (A ferroptosis-related gene signature predicts overall survival in patients with lung adenocarcinoma, Future Medicine, 2021). The genes that were finally used in the two studies for establishing the prognosis signature are different, but the concept, databases, and methodology as well as the conclusions drawn are almost identical.
One additional concern is that most of the genes, that eventually are used as prognostic markers in this study (e.g. DDIT4, IL33), do not constitute the core machinery of the ferroptosis pathway and only indirectly are involved in ferroptosis. SLC7A11 or GCLC that were initially identified as DEGs were not included in the five genes that formed the prognosis signature for LUAD. Based on the five-gene signature created in the current study, could somebody hypothesize that inhibition of ferroptosis is one of the factors involved in the development of lung adenocarcinoma?


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: ESTABLISHMENT OF A FERROPTOSIS-RELATED GENE SIGNATURE FOR PROGNOSIS IN LUNG ADENOCARCINOMA PATIENTS
Review round: 1
Reviewer: 3

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: In this study, Cai et al. proposed a bioinformatics study to find the ferroptosis-related gene signature for
prognosis prediction in lung adenocarcinoma patients. A comprehensive analysis has been conducted and the authors have found 5-gene signature for LUAD prognosis. The manuscript is well-written, there are some major points that can be addressed to improve the study:
1. The authors used datasets from TCGA and GEO also, did they concern about batch effect removal among data?
2. More literature review should be added in terms of bioinformatics analyses on LUAD.
3. Source codes should be provided for replicating the methods.
4. ROC curve has been used in previously bioinformatics studies i.e., PMID: 33539511 and PMID: 33260643. Thus, the authors are suggested to refer to more works in this description.
5. There should have space before "(", i.e., genes(259) ==> genes (259).


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: ESTABLISHMENT OF A FERROPTOSIS-RELATED GENE SIGNATURE FOR PROGNOSIS IN LUNG ADENOCARCINOMA PATIENTS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have satisfactorily answered the points raised by the reviewers. I have no further comments.
Experimental design: No further comments.
Validity of the findings: No further comments.
Additional comments: The revised manuscript has been improved significantly, and most of my concerns have been addressed.


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: OPTIMIZING THE POWER OF HUMAN PERFORMED AUDIO SURVEYS FOR MONITORING THE ENDANGERED HOUSTON TOAD USING AUTOMATED RECORDING DEVICES
Review round: 1
Reviewer: 1

Output:
Basic reporting: There are a few clarifications needed (see 'General comments' section). The raw data are shared along with R code. I suggest that you provide the code that actually reads your data set in to R, with all the correct formats (separators, etc), instead of using '=read.csv(file.choose())'
Experimental design: no further comment
Validity of the findings: no further comment
Additional comments: This study examines detection probabilities of Houston toads at two localities where they are known to occur. The study makes use of data collected continuously using acoustic recording devices (ARDs) and then examines the rate at which calls were detected in 5-min intervals. This is used to evaluate the effectiveness of the guidelines for conducting presence / absence surveys for this species. The main results are that the current guidelines lead to rates of false absences that are far higher than 5%.

One general thought I had is that you had to assume that the detection process of ARDs followed by a classifier leads to the same non-detection rates as human observers would. I don’t think this is a big problem but should be treated a bit more explicitly. I think it would be helpful to acknowledge that the detection process consists of several components. If a site is occupied, the species may not be detected because the frogs are not in the pond at the time (not sure whether this applies to the Houston toad). If they are in the pond, they may not call at the time of the survey. If they are there and call, the observer / ARD may fail to record them. Which of these components are relevant for your study (from reading your ms I had the impression that the toads don’t always call but may be wrong in this)? And how similar are those components of the detection probabilities the same for ARDs and humans?

Line 53: do the guidelines specify what the goal of the surveys should be? 95% probability of detecting the species at a site where it occurs? Or is that not clearly specified?

Line 139 and following: clearly define what you mean by ‘sampling protocol’ and ‘survey scenario’ and then use these terms consistently. E.g. in line 187, you use ‘sampling protocol’ for the different survey durations, which is different from line 140.

Lines 186 – 188: explain in a bit more detail how you calculate the confidence intervals. Did you calculate the confidence interval for the detection probabilities as the 2.5th and 97.5th percentile from the 1000 repeat simulations? And then plug those into the equation in line 185?

Line 213: “average 17 (range = 15-30)”. Are these numbers correct? In all other cases, the average was closer to the middle of the interval.

One issue with the third survey scenario (where you explore more suitable environmental conditions) is that you test the method on the same data you used to develop it. This needs to be stated as a caveat and the results treated appropriately, i.e. as a proposed strategy that needs to be tested on new data. Your results are probably too optimistic.

Another caveat, and you mention this one, is that your study included just two sites that may be unusual in terms of density of the species. I think this is really important since abundance is often a key driver of detection probability. In this connection, you could also consider how your results relate to the fact that optimal survey effort depends on the goal of the assessment and if the goal is to establish absence with a certain probability, one also needs estimates of occupancy (Guillera-Arroita, G., J. J. Lahoz-Monfort, M. A. Mccarthy, and B. A. Wintle. 2015. Threatened species impact assessments: Survey effort requirements based on criteria for cumulative impacts. Diversity and Distributions 21:620–630).

Line 306: “...found that not all suggested weather criteria within USFWS (2007) were useful...” did you? You don’t describe how you analysed the effectiveness of individual criteria, although this could easily be done, for example by using logistic regression.

One main take-away message I got from this study is that one should really deploy ARDs if it is important to establish absence, and this is also a point you are making. I think you have a great opportunity to go a step further and explore how many days these devices would have to be left on site to establish absence with 95% and 99% (say) probability. I think that would make your argument much stronger and help towards establishing guidelines for using ARDs in such situations.

The information in Table 2 and Figure 1 is the same. Both formats are probably useful but the table could be given as an appendix.


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: OPTIMIZING THE POWER OF HUMAN PERFORMED AUDIO SURVEYS FOR MONITORING THE ENDANGERED HOUSTON TOAD USING AUTOMATED RECORDING DEVICES
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall, the basic reporting in this manuscript was good. The Introduction was structured well—it introduced the problem, placed the importance of the study in context, and concluded with the three objectives of this study. The Methods were clear in most places, though I found some aspects of the description of the simulation to be confusing (as outlined below in the Experimental Design section). I found the Results clearly presented and easy to understand. The tables and figure supported the text nicely, but in Table 1 it would be interesting to present the same summary statistics for dates when Houston Toads were not detected to provide a contrast that might indicate how limiting environmental conditions are with regard to toad chorusing. Also, in Table 2 and in the text of the Results, it might be best to just round up to the next integer for presenting the number of surveys required to be 95% confident in absence because surveyors are unlikely to do a fraction of a survey.

Some minor grammatical errors and suggestions are indicated in the attached commented pdf.
Experimental design: The manuscript presents original primary research within the scope of PeerJ. The research questions are well defined and relevant to conservation of species that vocalize, and they are presented clearly at the end of the Introduction. The Introduction further provides information about the knowledge gap filled by this research. The investigation was rigorous and performed to high ethical and technical standards. For the most part, the Methods were described with enough detail to replicate them, but I thought that some additional detail and clarity about the automated audio classifier would be helpful.

On lines 125–137, the authors do a nice job by providing a good amount of detail about the Kaleidoscope automated audio classifier’s performance. The sensitivity of the classifier was impressive (lines 130–131), and the authors provide information indicating that the calls < 3 s duration identified by the classifier were overwhelmingly false positives (lines 133–135). I was left wondering, however, about the false positive rate was for putative calls > 3 s in duration. This information would be useful for others seeking to use automated classifiers in their research.
Validity of the findings: The authors provide the underlying data in the supplemental files. Because this is an observational study, there are not controls per se, but the authors provide information on how the data were screened and vetted for quality control in the manuscript. The one exception, outlined above, is that I think additional information about false positives for calls > 3 s duration would be valuable information to present. The authors presented little speculation and their conclusions were well-stated and linked to the original research questions. Importantly, the authors addressed the potential that by selecting sites with high abundance for their study, detection probabilities could be biased high, and they caution readers that finding smaller populations will likely require additional effort (lines 239–241 and 301–303). I have two main comments that I think would improve the Discussion:

1)	On line 229 in the statement, “…result in a likelihood of false negative errors that is too high…,” I find “too high” to be so vague as to be of little use. What is an acceptable rate of false negative errors? Is it anything > 5%, as suggested by the focus on declaring Houston Toads absent with 95% certainty, or some other threshold? Please clarify. I found the statements “an increase is required” and “to adequately detect” on lines 249 and 250, respectively, similarly vague.

2)	In general, I think it would be beneficial to provide some further guidelines on survey design. Specifically, on lines 250–252, I think it would be useful to illustrate the total effort necessary for human observers using manual methods. For example, based on Table 2 (and rounding the number of surveys up to the next integer), under the optimized protocol 28 (20–49) 5-min surveys require 140 (100–245) min of total survey time, whereas 16 (13–22) 60-min surveys require 960 (780–1,320) min of total survey time. Aside from using ARDs, what survey duration would you recommend for future surveys? How do the findings outlined in the paragraph on lines 273–285 (number of days meeting survey criteria per year) factor into this recommendation? Is the cost of surveys a consideration, and if so, how does costs scale with survey duration and the number of surveys?
Additional comments: This manuscript addresses an important topic for conservation: When have we looked hard enough to declare a species absent from a site? The authors use detailed, continuously collected data from ARDs and a simulation study to evaluate three different scenarios for conducting manual auditory surveys for the endangered Houston Toad. Importantly, the authors identify environmental thresholds that improve the likelihood of detecting chorusing Houston Toads. Unfortunately, these conditions can be so limiting in some years that one can have little confidence that Houston Toads are absent from a site at which they are undetected. Overall, the manuscript was a joy to read and addressed an important and interesting topic.


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: REPHINE.R: A PIPELINE FOR CORRECTING GENE CALLS AND CLUSTERS TO IMPROVE PHAGE PANGENOMES AND PHYLOGENIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: This report describes Rephine.r, a pipeline to identify split genes in phage genomes, fuse them back and use them for the determination of core genes among phage clades. The tool is then applied to a phage genus Pbunavirus, and two subfamilies, Tevenvirinae and Studiervirinae. The report  finally shows the phylogeny improvements provided by the increased amount of single core genes after such cleaning up.
This work provides a very timely and useful tool for phage biology as a whole that will also help in the field of phage taxonomy. The methodology is clean and well exposed, I have no major point to raise, only suggestions for improvements.
1.	A correlative problem to gene split in phage genome analyses is the gene calling method itself, which needs to be adapted for phages. This is not addressed in this work, as it takes as entry point the output of the Anvi’o pipeline. Please describe in the Methods how is Anvi’o performing this step (which program, what minimal orf size, is some level of orf overlap permitted). Provide a comparison of the number of orfs called by Anvi’o and those present in the Genbank files of reference T4, PB1 and T7 genomes, which have been studied in depth.  Is there an option for alternative codes (as some huge phages appear to use such codes)?
2.	Lines 199-211: some clarification is needed. Line 199, « the extent of overlap within the alignment space », is this the multiple alignment? Line 204 : « within the alignment », this is again the multiple alignment probably. In addition, the explanation of this overlap calculation is somewhat unclear. It seems one is dividing the size of ORF intersection by the size… of ORF overlap (so it is the same)? Should A U B not be the size of the aligned positions in A and B?
3.	Table 1 and Figure 1: could you use the same term of « defragmented clusters » in both cases (Table 1 uses instead « gene clusters with a fusion »), or is there a subtle nuance here?
4.	Give the final SGC list (with annotations) for each clade (and indicate the new ones). Such information is insightful for taxonomists.
5.	Fig3 and Suppl Fig2: label the leaves, at least one phage in each group. Are the Tevenvirinae shown at the very root of the tree real ones, or rather falsely classified phages?
6.	The number of remaining paralogs in each clade is high. What kind of function do they encode?
7.	Check the supplementary figure legends, I could not find them but they may be hidden somewhere in the files.


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: REPHINE.R: A PIPELINE FOR CORRECTING GENE CALLS AND CLUSTERS TO IMPROVE PHAGE PANGENOMES AND PHYLOGENIES
Review round: 1
Reviewer: 2

Output:
Basic reporting: This manuscript introduces Rephine.r, which is a novel type of tool to assist phage pangenome analysis. Pangenome analysis of phages are not very popular so far but must be promising to characterize phage lineages. The manuscript is clearly written, and the developed pipeline is well designed to overcome the potential difficulty of phage pangenome analysis.
Experimental design: The main pipeline of Rephine.r is composed of two parts, (1) merges remotely related gene clusters and (2) fuses fragmented genes. Each component is effective for phage pangenome analysis. Especially, the second component includes high originality, and it is applicable for various cases as is discussed. However, I considered that only ‘the degree of overlap in the alignment’ is enough to discriminate the true and false gene separation and did not understand why sequence dissimilarity is needed to be evaluated. It would be better to discuss the case of low overlap and high similarity (more than 10 cases exist, as shown in Suppl. Fig 1).
Validity of the findings: All conclusions are valid.
Additional comments: 1. This work provides much improvement to phage pangenome analysis. Nevertheless, I suggest one point that might be better to be discussed. If a gene is completely missed in the original gene call, the gene is not rescued by the current implementation of Rephine.r. Merged use of multiple gene caller, including phage specific ones such as PHANOTATE, will provide further improvement. Is it possible to incorporate this step into Rephine.r?
2. L169 includes an empty parentheses.


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: REPHINE.R: A PIPELINE FOR CORRECTING GENE CALLS AND CLUSTERS TO IMPROVE PHAGE PANGENOMES AND PHYLOGENIES
Review round: 2
Reviewer: 1

Output:
Basic reporting: The manuscript is now ready for publication.
Experimental design: OK
Validity of the findings: OK
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: REPHINE.R: A PIPELINE FOR CORRECTING GENE CALLS AND CLUSTERS TO IMPROVE PHAGE PANGENOMES AND PHYLOGENIES
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The manuscript is significantly 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: GENOME-WIDE ANALYSIS OF THE LIGNIN TOOLBOX FOR MORUS AND THE ROLES OF LIGNIN RELATED GENES IN RESPONSE TO ZINC STRESS
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: No additional comments


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

Input:
Title: GENOME-WIDE ANALYSIS OF THE LIGNIN TOOLBOX FOR MORUS AND THE ROLES OF LIGNIN RELATED GENES IN RESPONSE TO ZINC STRESS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Most of the text is well-written, with no grammar mistakes, but some sentences are poorly written. For such sentences, I made suggestions that might help the authors.

I think the authors should cite more studies reporting the determination of the lignin toolbox in other species. More references on some key aspects of Morus (such as zinc stress in such species) might also be useful.

The structure of the article is acceptable. However, I have the suggestion to organize the gene families according to their order in the biosynthetic pathway. Currently, it may confound the reader. The figures are of good quality, but sometimes there are too much information on the phylogenetic trees, so the reader cannot depict the genes/proteins in the terminals.

Because the authors consider both species as "morus", sometimes the article becomes confusing. For example, when determining the toolbox based on the hierarchical clustering, I don't think considering all genes as from the same species is correct and this leads to wrong conclusions.
Experimental design: The research is original, as this is the first attempt to determine the lignin toolbox in mulberry.

Although the research question is well-defined, I think the authors should clarify their criteria to select their target genes. This is very confusing throughout the manuscript. The first part of the results section should present all the criteria and what would be consider a "good candidate". The authors should also include a conclusive sentence at the end of each section (i.e. for each gene family).

One major concern regarding the experimental design: the RNAseq data exploited to survey the lignin biosynthetic genes in M. notabilis do not include xylem tissues (or, at least, stem tissue), which are considered a hotspot for lignin deposition in woody species such as those of the Morus genus. As the authors did not provide detailed information on the tissues samples used for RNAseq and RT-qPCR analyses, it is hard to correlate gene expression with lignin deposition, which makes their criteria weaker. In the case of M. notabilis, the authors should have include another step within their pipeline to identify the lignin toolbox: RT-qPCR analyses in tissues contrasting for lignin deposition. This becomes obvious when analyzing the CAD family, for which expression data are not avaliable for the two most important candidate genes.

Methods are not described with sufficient details. Please see my comments below.
Validity of the findings: The selection of candidate genes for the lignin toolbox in mulberry is not completely reliable. While pertinent for some gene families, for others the expression pattern of some selected genes is not consistent with lignification. More importantly, the search for SmF5H homologues in mulberry does not make sense, as this gene belong to a clade that especifically evolved in Selaginella. The lack of a tissue considered as a "reference tissue" for lignification in their dataset for M. notabilis (i.e. xylem tissues) is another drawback of their exeprimental design.

Another concern is that the authors aim to determine the "role of lignin-related genes in zinc stress". However, they only analyzed the expression of the so-called lignin toolbox, which was determined based on developmental lignification. It is known that plants may employ different paralogues for each gene family when comparing developmental versus stress lignification. Therefore, to really understand this response, the authors should have analyzed all 49 genes found for the species.
Additional comments: - Line 18: it is important to explain what “ramulus mori” is
- Line 24: the sentence “Genes in the bona fide clade were focused on” is confusing; did you mean that you have focused on bona fide genes?
- Line 28: the process of naming your target species is a bit confusing; in the abstract, the reader can find Mulberry, ramulus mori, Morus notabilis, Morus alba variety Fengchi and morus; this problem is particularly relevant when you claim that the lignin toolbox was determined as 19 genes in morus; does the expression “morus” refer to species in the Morus genus? Wouldn’t be better to use “mulberry” as the general name?
- Line 45-27: well, this is actually not true; the monolignol biosynthetic pathway refers to the branch of the phenylpropanoid pathway leading to the synthesis of hydroxycinnamyl alcohols
- Line 53: the abbreviation for p-coumarate 3´-hydroxylase is C3´H (this is important because the recently characterized ascorbate peroxidase – APX – showing the ability to 3´-hydroxylate p-coumarate to caffeic acid is named C3H -> without the apostrophe)
- Line 53-55: please be careful with chemical nomenclature: 5´-hydroxylase and the “O” should be in italic in the name of the transferases
- Line 60-61: I understand that CCR and CAD are monolignol-specific enzymes, but why is 4CL included in this sentence as the “primary pathway for monolignol biosynthesis”?
- Line 66: please, explain here what “ramulus mori” is
- Line 70: with this sentence, are the authors referring to other studies reporting “lignin toolbox” for other plant species? Because if yes, these references are not appropriate
- Line 78: please explain why did you include M. alba variety Fengchi in this study; why was it important?
- Line 83-86: it is also not clear why did the authors decide to study the stress caused by excess of zinc; is this particularly important for mulberry production? Why not any other abiotic stress?
- Line 92-96: about the zinc treatment, is there a reference for this specific experimental design? I have several questions: i) why 450 mg/kg? ii) samples were harvested only at T=0 and after 15 days of treatment? Iii) why was the zinc stress analyzed only in Fengchi? iv) how old exactly the seedlings were? One year old? Why to analyze this in young seedlings? v) when the authors mentioned “three biological replicates”, did they mean only three individual plants per treatment?
- Line 103: what would be “SmF5H”?
- Line 112: in which database your data was deposited?
- Line 121: I suggest “The gene expression based on the large-scale transcriptome data was calculated…”
- Line 122-123: by realizing that RNAseq data are available for M. notabilis, it is even more important to explain why Fengchi was included in this study
- Line 122-123: the authors should provide detailed information on the tissue samples used for RNAseq and RT-qPCR analyses; were these tissues from adult plants? how old were the plants? In the case of roots, were they mature and lignified?
- Line 136: “monolignin” is not a correct term; please use either monolignol biosynthesis pathway or lignin biosynthesis pathway
- Line 141: here we have the first relevant information on Fengchi; but not only this is not enough but also is misplaced in the manuscript
- Line 146: the deamination of Phe into cinnamic acid is the initial step of the phenylpropanoid pathway in every plant species, not only woody plants; the only remark on this topic is that grasses harbor PALs that are able to use tyrosine to produce p-coumaric acid, by passing the reactions catalyzing by PAL + C4H
- Line 147: the authors should be consistent throughout the manuscript: the heatmap indicating gene expression data on PAL genes is represented in a different way when compared to the other gene families (genes in rows, not in columns)
- Line 147: I’m not sure that it is a good idea to adopt the abbreviation for the Fengchi genes (FcXXX) as it is; I mean, this is a variety but not a species, so your method is not really following what has been done for all other species; this can cause confusion in the future
- Line 156: the sentence “MnPAL1 and 5 showed an expression preference in the lignification of organs and tissues” does not make sense; are the authors trying to claim that the expression of such genes is preferential in these tissues?
- Line 156: also, the authors should make it clear to the reader which is the expression pattern expected for a gene to be involved in lignification in their panel of tissues; in this regard, my criticism is that the authors didn’t include “xylem tissues” in their analyses, which would be the best target for identifying lignin-related genes
- Line 168-169: why MnPAL2 and MnPAL5 are not considered strong candidates as well?
- Line 175-178: there is wrong information in the text; At4CL3 is the divergent one (Clade II), not At4CL2
- Line 176-178: the expression pattern of MnPAL4 is not consistent with lignification; the authors shouldn’t pool the description of all genes together because this is misleading
- Line 190: I suggest the authors include a conclusive sentence at the end of each section reporting the selected candidate genes to be part of the lignin toolbox in mulberry (as they did for PAL)
- Line 191: I suggest the authors to organize the description of each gene family according to their sequence in the pathway, not according to the type of reaction they perform; otherwise, it can get a little bit messy (and confusing for readers not familiar with the lignin biosynthetic pathway)
- Line 191: I have several comments for the section on the “hydroxylation steps”; 1) C3´H is not part of the general phenylpropanoid pathway (which consists of only PAL, C4H and 4CL); 2) C4H and C3H are not responsible for the production of all hydroxycinnamates, but ONLY p-coumarate (C4H) and caffeic acid* (*if C3H = APX, not CYP98); 3) the authors seem to confound C3´H (CYP98A3) with the recently characterized C3H (which is an ascorbate peroxidase); C3´H (CYP98A3) is responsible for the 3´-hydroxylation of p-coumaroyl shikimate into caffeoyl shikimate; in poplar, the protein complex made of C4H and C3´H was reported to catalyze the hydroxylation of p-coumarate to caffeic acid (Chen et al, 2011; doi: 10.1073/pnas.1116416109), but this has not been reported for any other plant species; C3H/APX is a bifunctional ascorbate peroxidase that not only uses ascorbate as substrate but also has the ability to convert p-coumarate into caffeic acid (Barros et al., 2019; doi: 10.1038/s41467-019-10082-7)
- Line 207: from which species is StC3H? my suggestion would be to include always the same plant species, for all gene families, for which a good amount of lignin biosynthetic genes have been functionally characterized
- Line 217: another mistake: the shikimate shunt, stated by the activity of HCT, channel the carbon flow away from H and towards the biosynthesis of G and S
- Line 219: HCT catalyze the acylation of CoA esters with shikimate, producing shikimate esters; please correct
- Line 243: why so many CSEs in the corresponding phylogenetic tree? Again, I suggest the authors to use the same plant species for all gene families, for organization reasons; the exception should be in cases it is particularly important to include additional proteins (such as HCT versus HQT)
- Line 244: regarding the CSE phylogeneny, previous studies have demonstrated that what we call a bona fide CSE with a function in lignification might be the result of a neofunctionalization within the monoacylglycerol lipase family (Ha et al., 2016; Kim et al, 2016; doi: 10.1111/tpj.13146); all other CSE-like genes are most likely MAGs; please, consider this in your phylogenetic analysis and when suggesting a function for CSE-like genes in lignification
- Lines 253: CCoAOMT is important for the synthesis of both G and S units
- Line 255: in figure 4, several CCoAOMT names in Clade I are overlapping, so it’s impossible to know which protein is which
- Line 281: please correct this sentence (remove “5-hydroxylas”)
- Line 289-290: in my opinion, it does not make sense to search for putative homologues of SmF5H in Angiosperms and, more importantly, to consider this strategy for this paper; in the original paper reporting the discovery of this gene (Weng et al., 2008; doi: 10.1073/pnas.0801696105) the authors performed phylogenetic analyses and concluded that SmF5H “belongs to a unique clade of Selaginella P450s that is distinct from all of the known P450s, suggesting an independent origin of F5H in Selaginella.”; so, the more closely related genes to SmF5H might be merely members of the more closely related CYP98 and CYP75 families
- Line 307: again, this remark on 4CL should be removed
- Line 312-314: please explain why bona fide CCRs should be considered CCR-like (this statement is contradictory, as a CCR-like gene necessarily indicates that it is not a bona fide gene); I believe the sentence is grammatically wrong
- Line 319: what is exactly “motif-aware analysis” and where can I find its corresponding results?
- Line 321-322: why exactly CAD is responsible for “the diversity of monolignols”? This enzyme catalyzes the same reaction for all lignin subunits, can could it contribute to the chemical diversity of such compounds?
- Line 324-326: this sentence is confusing; which enzyme was reported to be a CAD-like without detectable CAD activity in vitro?
- Line 328-329: because no expression data for MnCAD3 and 4 are available in Morusdb and no further expression analysis was performed, there is no further support for their role in lignification apart from the phylogenetic analysis; that’s why the authors should have provided RT-qPCR data also for M. notabilis
- Line 336: I don’t think the expression data support the role of FcCAD1 in lignification
- Line 340-343: the problem here is that you didn’t indicate which genes are “=-like” genes for each family; for some families (such as CCR), this is mentioned in the text, but the name of the genes should include this classification, so the reader can follow the story; first, you should describe what were the criteria to classify a gene as bona fide and as “-like”, then indicate in the text and in the figures, which genes belong to each classification (by just using “-like” in the abbreviation of each gene)
- Line 343: what should the reader understand with “(27/31)”? does it refer to the number of bona fide genes in each of the two Morus species?
- Line 341-348: regarding fig. S4, I think it is a great idea to perform hierarchical clustering for all the genes to further evaluate whether the selected toolbox indeed show a similar expression pattern (and, thus, cluster together); however, I’m confused by the fact that the authors apparently considered the orthologous genes in the two different species of morus as the same gene in this analysis; moreover, then they claim that RT-qPCR analysis “validated the expression preference in lignified organs for the lignin-related genes comprise the lignin toolbox in mulberry”, but then only genes from Fengchi were analyzed; finally, which genes are considered the lignin toolbox in mulberry then?
- Line 350: so, apparently the authors evaluated the expression of the pre-selected lignin toolbox in Fengchi plants upon zinc stress; however, it is well-known that stress lignification may employ different paralogues than developmental lignification; so, the correct design should be to include all genes in this analysis and evaluate which one respond more drastically to zinc stress
- Line 364-365: can the author explain how exactly tandem duplications were analyzed?
- The discussion of your manuscript is very limited; you should better exploit your findings


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

Input:
Title: GENOME-WIDE ANALYSIS OF THE LIGNIN TOOLBOX FOR MORUS AND THE ROLES OF LIGNIN RELATED GENES IN RESPONSE TO ZINC STRESS
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: No additional comments


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

Input:
Title: GENOME-WIDE ANALYSIS OF THE LIGNIN TOOLBOX FOR MORUS AND THE ROLES OF LIGNIN RELATED GENES IN RESPONSE TO ZINC STRESS
Review round: 2
Reviewer: 2

Output:
Basic reporting: The manuscript is much improved from the first submitted version. The authors addressed most of my concerns and nicely follow my suggestions (which, by the way, they are not obliged to do so...).
I have minor issues, mostly regading the writing.
Please see below.
Experimental design: No remarks.
Validity of the findings: No remarks.
Additional comments: - Title: including the suggesting to use “mulberry” instead of morus, my suggestion for the title is “Genome-wide analysis of the lignin toolbox of mulberry and its role in the response to zinc stress”
- line 24: no need for “and lignin-related genes” here
- line 29: instead of claiming that “We also indicated the important roles of lignin-related genes in response to stress” I suggest something like “We also observed changes in the expression of some of these lignin biosynthetic genes in response to stress”
- line 39: “efficient conversion”
- line 49: “… and provides hydroxycinnamoyl-CoA esters…”
- line 60-61: “CCR and CAD constitute the primary pathway…”
- line 77-79: my suggestion “The availability of the Morus notabilis genome and an increasing number of transcriptomic data for mulberry allows comprehensive genome-wide analyses of lignin biosynthesis genes in this species”
- line 84: please separate these two sentences (also some suggestions for the second sentence); “M. alba is one of the most widely cultivated mulberry in China. M. alba variety Fengchi is a new variety created by Sericultural Research Institute, Chinese Academy of Agricultural Sciences, expected to spread and grow in extreme environment conditions and used as heavy metal hyperaccumulators and forage.”
- lines 90-93: “We also assessed the potential roles of lignin biosynthetic genes in response to stress caused by the excess of zinc in Fengchi and proposed that the promotion of lignification in lignifying organs, associated with the inhibition of lignin deposition in leaves, is an important response to zinc stress in mulberry”
- line 143: the correct abbreviation is RT-qPCR
- line 146: lignified or lignifying? I guess the second fits better
- line 155: “monolignol”
- line 160: Morus alba (not morus)
- line 173-174: I guess the information on the function of PALs with anthocyanin biosynthesis refers to the Arabidopsis PALs, correct? So, a minor change in the sentence is needed: “… are phylogenetically close to AtPAL1 and AtPAL2, which have been reported…”
- line 175: “MnPAL1 and 5 are preferentially expressed in lignifying organs and tissues…”
- line 213-214: this information on the C4H-C3’H complex should appear after the explanation of each enzymes function, not before; in addition, the authors should make clear what functionality this enzyme-enzyme association allows
- line 223: my suggestion here is “Although C3’H was shown to catalyze the conversion of p-coumaric acid into caffeic acid in vitro, further studies demonstrated that its activity in vitro is the conversion of p-coumaroyl shikimate to caffeoyl shikimate”; (please, also cite Schoch et al., 2003; doi: 10.1074/jbc.M104047200)
- line 228: it is not clear which other MnC3’Hs and FcC3’Hs are mentioned here
- line 229: “C3’H” not “C3H”
- line 233: “C3’H” not “C4H”
- line 238: “to change the carbon flux from H to G and S lignin units”
- line 246: “to distinguish”
- line 249: “sequence similarity”
- line 259: “AtCSE was first characterized as lysoPL2, a member of the monoacylglycerol lipase (MAGL) gene family in Arabidopsis”
- line 289: COMT is not considered an enzyme involved in the biosynthesis of G lignin
- line 310-315: I again insist in the fact that searching for “homologues” of SmF5H in Angiosperms does not make sense here; as I mentioned in my previous report, this genes was shown to have evolved independently in Selaginela; therefore, all the apparent “homologues” identified here are very distantly related and do not represent genes with similar function anyhow
- line 332-333: “and converts various cinnamoyl-CoA esters to their corresponding hydroxycinnamaldehydes…”
- line 368-369: this sentence is confusing; maybe the authors wanted to claim “Hierarchical clustering depicted a similar expression pattern for bona fide lignin biosynthetic genes, which differed from that of genes identified as ‘like’ genes”
- line 368-377: my suggestion to the authors is that they include, in this paragraph, their conclusion on their definition of the lignin toolbox in mulberry; in other words, they should list here which were the genes considered the lignin toolbox in this species; additionally, they should highlight these genes in Fig. S6 (maybe by just including an asterisk in front of the gene name); this would facilitate our understanding
- line 379: the beginning of this sentence is hard to understand; can the authors rephrase, please?
- line 384: “Most of these bona fide clade genes (13/22) were down-regulated in leaves.”
- line 412: “leads to oxidative stress”
- line 414-415: this sentence is confusing; please rephrase it


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 ERLANG DISTRIBUTION APPROXIMATES THE AGE DISTRIBUTION OF INCIDENCE OF CHILDHOOD AND YOUNG ADULTHOOD CANCERS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Mostly ok, but needs better referencing of prior work.
Experimental design: Assumptions made in their modeling are overly simplistic, and key parameters like stem cell population size and how it changes with age are not considered.
Validity of the findings: The results of their modeling, such as for numbers of driver events for different cancers, are not substantiated and do not appear consistent with those from cancer sequencing projects.
Additional comments: Belikov and colleagues use various probability models to determine the best fit to the incidences of different childhood and young adult cancers. Understanding the reasons for early life incidences of cancers is clearly important. They present data to claim that that the Erlang/gamma distribution best approximates these incidence curves. From what I can tell, they are exploring two parameters of cancer causation – the occurrence of mutations and their timing.  There is no consideration of population size (i.e. for the stem and/or progenitor pools where cancers initiate), mutation rate or the microenvironmental parameters that dictate somatic evolution, nor how these parameters can change quite dramatically with age (from conception to old age). In addition to be overly simplified, I believe this work suffers from over “model fitting”, where one can always find parameters to fit some model, even if the model tells us little to nothing about reality. Moreover, I do not see how their modeling explains the decline in the incidence of these cancers after their early peaks.

Specific concerns:
1) They claim that the Poisson distribution of cancer incidence can be explained by the waiting time for some event (presumably a mutation or epimutation), but why does incidence then fall with the same kinetics that it rose, given that the vast majority of the population remains unaffected?  Previous work (from my group) has shown how consideration for how the stem cell pool size changes from conception through childhood can provide at least one reasonable explanation (1, 2). The authors should also consider the work of Mel Greaves on the early risks of childhood leukemias (3, 4).

2) They estimate the numbers of drivers for different cancers of youth; for example, they estimate 8.95 drivers for gonadal germ cell tumors.  No attempt is made to link these estimates to the known genetics of these cancers (similarly, their estimates for driver numbers for cancers of old age, in their 2017 Scientific Reports paper, are similarly unsubstantiated).

3) This worked is based on the assumption that “cancers develop upon acquiring a particular number of (epi)mutations in driver genes”. While this is still often accepted, numerous studies have demonstrated that this model ignores key parameters of evolution (like context-dependent selection, for which there are now numerous demonstrations). See for example this review (5).

4) The authors have referenced some classic papers on the age-dependence of cancers, but are missing many others.

5) The goodness of fit often was in the range of R^2 of 0.9 or better, the result of a grid search for combination of parameters that maximized this R^2. Thus, parameters can be found that fit the data, but there’s no indication that these parameters have any basis in reality.

Signed: James DeGregori

1.	Rozhok A, DeGregori J. A generalized theory of age-dependent carcinogenesis. eLife. 2019;8:e39950.
2.	Rozhok AI, Salstrom JL, DeGregori J. Stochastic modeling reveals an evolutionary mechanism underlying elevated rates of childhood leukemia. Proceedings of the National Academy of Sciences of the United States of America. 2016.
3.	Greaves M. Infection, immune responses and the aetiology of childhood leukaemia. Nature reviews Cancer. 2006;6(3):193-203.
4.	Greaves M, Cazzaniga V, Ford A. Can we prevent childhood Leukaemia? Leukemia : official journal of the Leukemia Society of America, Leukemia Research Fund, UK. 2021.
5.	Solary E, Laplane L. The role of host environment in cancer evolution. Evolutionary applications. 2020;13(7):1756-70.


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 ERLANG DISTRIBUTION APPROXIMATES THE AGE DISTRIBUTION OF INCIDENCE OF CHILDHOOD AND YOUNG ADULTHOOD CANCERS
Review round: 1
Reviewer: 2

Output:
Basic reporting: See attachment for details.

There are places where unsubstantiated claims are made, but I think this may be due to poor English skills.
Experimental design: See attachment for details.

There is a key paragraph that explains the method of fitting the data, that I could not follow. I think this needs improving.
Validity of the findings: See attachment for details.

There is a key paragraph that explains the method of fitting the data, that I could not follow. I think this needs improving.
Additional comments: Overall, I think this is a worthwhile paper, and I hope it can be improved and corrected, for example as suggested in my attachment.


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 ERLANG DISTRIBUTION APPROXIMATES THE AGE DISTRIBUTION OF INCIDENCE OF CHILDHOOD AND YOUNG ADULTHOOD CANCERS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The paper is well written (there are a few grammatical mistakes, but minor). Referencing is more balanced in the revised manuscript.
Experimental design: The authors now better acknowledge the role of the tissue microenvironment (basically, in terms of how it influences the "driverness" of a mutation).  I still think that they should consider, or at least acknowledge, that the population size of stem cells, which obviously dramatically changes from conception to maturity, will influence cancer rates - essentially, the target population for mutations is changing. In addition, tissue microenvironments change (particularly in old age).  That said, I do not expect that every model of cancer will focus on the same parameters that we find important, so I do not expect the authors to change their modeling methods. But simply acknowledging that parameter changes with age should influence cancer rates, even if not incorporated into their models, would increase the balanced nature of the work.
Validity of the findings: The modeling appears sound (noting that I do not have the mathematical expertise to judge their methods, although Rev #2 appears to). They now better indicate that their modeling shows what "could be" not what "is".
Additional comments: I think that it's important for science that different views are encouraged even when they disagree with the views and results of the reviewer (me). The authors did do a good job addressing concerns, with the minor exceptions noted above (particularly for stem cell pool size changes with age). In all, their work does make a meaningful contribution to the overall debate for how cancer incidence varies as a function of age. I am choosing "minor revisions" simply to provide the authors with the opportunity to acknowledge the shortcomings of their modeling in terms of considerations of population size (stem cells) and tissue microenvironments and how these CHANGE with age.


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 ERLANG DISTRIBUTION APPROXIMATES THE AGE DISTRIBUTION OF INCIDENCE OF CHILDHOOD AND YOUNG ADULTHOOD CANCERS
Review round: 2
Reviewer: 2

Output:
Basic reporting: This is now much clearer. I have suggested a handful of minor changes to the text to improve the language - see attachment.
Experimental design: I have not checked the code, but I have no reason to doubt its validity. It was unclear what the data was that is in the repository with the code. It appears to be some form of summary data. An improved description of that data is needed.
Validity of the findings: As far as I can tell, the findings seem valid.
Additional comments: I think the article is much better, I have suggested a small number of minor alterations to improve the text and explain things better.


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: CONGRUENCE BETWEEN MORPHOLOGY-BASED SPECIES AND BARCODE INDEX NUMBERS (BINS) IN NEOTROPICAL EUMAEINI (LYCAENIDAE)
Review round: 1
Reviewer: 1

Output:
Basic reporting: -I recommend using the same format in bibliographic references, sometimes some have the full name of the journal, sometimes not.
- In Table 2, second column says ‘Indivuduals’ it should says ‘Individuals’
-Please, it´s necessary to verify some values and links, more details in the manuscript.
- There some spelling errors that are marked in the manuscript.
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The manuscript is worth publishing.


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: CONGRUENCE BETWEEN MORPHOLOGY-BASED SPECIES AND BARCODE INDEX NUMBERS (BINS) IN NEOTROPICAL EUMAEINI (LYCAENIDAE)
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall, this paper is organized in a clear way. While I am not a native English speaker, I noticed that English is not perfect throughout, though the problems seem to be mostly minor ones. Particularly in the discussion, there are several claims about previous findings without references (e.g. sentences ending on lines 210, 225 and 250). In general, and again particularly in the discussion, the used literature is not extensive enough and many important papers have not been considered. The figure captions are not very clear and well-written (e.g. the sentence "Each point represent the collecting site of each individual" in Fig. 1 caption). The figure 2 and 3 caption start by saying "Three scatterplots are provided..." but there are nine in each.
Experimental design: The paper publishes an important and remarkable dataset of South American butterflies and clearly merits becoming published. The set research questions are relevant and meaningful, although the used methods are not particularly sophisticated. For example, the authors are concluding things based on visual patterns seen in the scatterplots, but their observations are very difficult to verify and as the differences were not shown to be statistically true, it is not easy to confirm if the patters actually even exist. It would not have been difficult for example to statistically (ANOVA etc.) investigate if the divergence patters (intraspecific variation, distances to NN) differ between the sets of species occurring in different altitudes. It could even be studied statistically (regression) if altitude has an effect to the mentioned patterns of divergence. I find the lack of statistics a clear weakness in this paper as, indeed, it is not clear if the "observed" patterns really hold true. The methods are described mostly in a sufficient manner. The authors used mostly standard analytical tools of BOLD that is not wrong, but some fine-tuning of the figures would not hurt (for example, due to a bug in the BOLD tools there is not space after the words "Dist"/"NN" and "(%)".
Validity of the findings: As stated above, the generated data is valuable and extensive. The data is made publicly available. I would find the overall logic of the discussion the weakest part of this manuscript and would like to elaborate this opinion further. First, the authors conclude (from line 335) that "relatively young species in young ecosystems tend to have more incongruences...". Actually, this represents circular reasoning. The thing that the species are young is based only a low sequence divergences. No more rigorous evidence for the young age is presented, although indirectly this is supported also by the relatively young age of the ecosystems they are inhabiting. Therefore, if young species are defined by small divergences, it is hardly surprising that young species are having small divergences. What else it could be, because it is so by definition? Second, what do the author mean by young age of species? All species have equally long evolutionary history. A species may turn to another species without a split of the lineage, or they may "technically" become new species as a result of such a split. Exactly, when do the authors think the new species was born? Is there evidence that the mutation rate of different lineages keeps constant? This question is further complicated by the fact that intrinsically (this is not discussed) it seems evident that the authors use different criteria for "species" under different connections. As they are discussing the hybridization and gene flow in several occasions, it seems that they think species being more or less reproductively isolated entities. But then they are telling that montane species are typically allopatric. How much do we know if the allopatric populations/species are capable to reproduce with each other? I feel that the authors are deep in the swamp what comes to the age of the ages of species and how they decipher the term species. Additionally, they seem to have adopted an opinion that they "know" where the true species limits lie. This is apparent also in the other sections of the paper as the functionality of DNA barcoding is compared to the prevailing taxonomy, but it is not discussed at all how accurate/inaccurate this taxonomic framework could be. Maybe there are false species included. Maybe some of the allopatric populations on montane species are not valid species at all (whatever it means as delimitation of allopatric populations is inherently arbitrary). I find that the discussion does not consider factors like these to the sufficiently degree. It is certainly tempting to rely on the idea that clear boundaries between species really exist, but this is hardly true. By this I do not mean that these matters should not be discussed at all. My point is that I find the discussion not very in-depth and not considering all relevant aspects. Third, the introduction sets some hypotheses that however are not explained and lack references. Especially it should be explained why the authors want to study the hypothesis (line 118) that the power of DNA barcodes decreases along with the altitude. This is discussed, weirdly, in more detail in material and methods, in lines 166-180. I find that this section would fit much better to the introduction. However, the reasoning in this section lacks any references. They also refer to their own previous studies (line 166) but do not give a reference.
Additional comments: Despite some criticism, I find the data and findings of this paper valuable and I am happy to recommend it after moderate revisions. Besides my comments above, I would like to raise some smaller issues:
Line 156: please clarify "outcome is deterministic". I don't understand what this exactly means.
Line 556: Although not many individuals per species was analyzed, the authors found a remarkable number of intraspecific BIN splits. It would have been nice to see this assessed by statistical means. How many splits could be expected if all species were sampled by, say 20 individuals? This value is naturally an underestimation, but this is not discussed.
Line 218: "...it is most likely that they can be validated as two different species". I do not find such things as questions of likelihood. It is more a question of how we define the term "species". I would leave the likelihood thing out and just write. "...is highly divergent, they can be validated as two different species, particularly is both entities...".
Line 251-252: Wolbachia does not itself result in barcode splits. It may mediate spread of introgressed mitochondria in a new species. These bacteria do not cause mutations but may greatly affect to the allele frequencies.
Lines 264-265: "...we suppose that such processes in high Andean species occur more frequently". This requires elaboration. Why do you think this being the case?
Line 268: "Phylogenetic results" is a bit weirdly stated. Perhaps "phylogenetic patterns"
Line 279-280: Here you give an idea that DNA taxonomy is about use of DNA barcodes in species delimitation that is not true. DNA taxonomy desires using multiple genes in species delimitation.
Lines 300-301: What is the true evidence that the species have evolved since the last glacial maximum? Is this based just on low genetic divergences?
Lines 309-310: All algorithmic species delimitation methods are based on arbitrary a priori settings and assumptions. It is exactly because of this what makes delimitation of species inherently arbitrary, especially with allopatric populations.
Line 314: This sentence includes an idea that a single the "true" taxonomy really exists.
Line 322: How can you know that in this case this happened in short period of time? It is a widespread problem in this manuscript that somehow, magically, you "know" how old different species are.

Small grammatic issues:
Line 87: The word "Lepidopteran" should not be capitalized'
Line 227: italicize "Rhamma"
Line 284: Remove and extra comma (not sure if this sentence makes good sense, by the way; certainly all continents have a long geographic history)
Line 292: intrincated > intricated

Reference section is with many inconsistencies and small glitches. Just in the first line (359) there are two such glitches (extra "s” and a lacking space). Some journals are abbreviated, some not. Line 374 gives "pp." for a journal article. After the volume number, both comma and colon are used. Line 448 is with species name without a space. Line 468 lacks the volume and page range. It varies after how many authors "et al." is used in the authors list. Lines 499 and 500 are both with an extra space. Line 553 is with two words together. Lines 570 and 571 are with extra hyphens. Some scientific names in article titles are italicized, some not. Just to mention some examples.