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: FROM MORPHOLOGY TO MOLECULES: A COMBINED SOURCE APPROACH TO UNTANGLE THE TAXONOMY OF CLESSINIA (GASTROPODA, ODONTOSTOMIDAE), ENDEMIC LAND SNAILS FROM THE DRY CHACO ECOREGION
Review round: 1
Reviewer: 1

Output:
Basic reporting: This paper is original and constitutes an important and valuable progress in the knowledge of the endemic gastropods from Argentina. It discusses the taxonomy of genus Clessinia using multiple sources: shell and anatomical morphology, shell morphometry and molecular data. A molecular phylogeny is presented and the authors discuss a previous hypothesis of paraphyly for Clessinia and Spixia.
The manuscript is clearly written in professional English and well organized. The title is accurate and the abstract summarises correctly the study´s content. The introduction and literature cited account correctly the background information. Figures and tables are clear and relevant to the content of the article. All data provided as supplemental files
Experimental design: The paper consists of original primary research.
The research hypotheses are clear and relevant to clarify the taxonomy of genus Clessinia.
The investigation was conducted rigorously, the methods are reproducible and adequate to test the hypotheses proposed.
The two morphometric analyses performed (lineal and geometric) showed similar results.  Please consider eliminate one of them to reduce the length of the manuscript.
A phylogeny based on morphology and a discussion of evolution of characters and consistencies/inconsistences with the molecular phylogeny would be desirable. Please explain why you decided not to perform this kind of analysis.
Validity of the findings: The multiple-source data provided in the paper to test hypotheses of species delimitation in genus Clessinia are accurate and support the conclusions.
Additional comments: Please, consider the following suggestions to improve the article:
-Line 178. Material and methods: Please include the number of specimens (shells and living ones) used for anatomical descriptions and molecular analyses
- Line 207: 10 specimens from each species or subspecies is a small sample size to perform a morphometric analysis. The variability within and among species can be underestimated and some overlap could not be detected. Please, consider redoing the analysis with a higher N of each taxon.
- Regarding geometric morphometry, as landmarks are considered homologous morphological loci, please explain how you could determine homologous landmarks in whorl sutures in snails with different whorl number. (In case, you consider only snails with the same number of whorls, some variability is missing)
-Line 342, 343, 351. I suggest using only “lamellae” here and employing “teeth” in the context of digestive system (radula).
-Line 657. Please include Remarks to compare the subspecies C. stelzneri stelzneri and C. stelzneri striata
-Line 1076 and the following ones. Discussion of the coat of sand granules in haired shells.
Line 1090. Authors stated: “Strikingly dryer habitats hold the species with longer hairs…” Please clarify why this fact is strikingly. May be, the authors could discuss Pfenninger et al. (2005) [Why do snails have hairs? A Bayesian inference of character evolution].
The authors explained correctly that ornamentation of shells could be adaptive (anti-predatory/reproductive behavior) or passive (a by-product of the passage through a sticky substrate or by the adherence to ribs, hairs or spines on the shell). The adaptive explanations must be tested through a series of experiments to demonstrate heritability and variability of the character, correlation between the character and fitness different from 0, etc. Therefore, adaptive explanations in the current state of knowledge are speculative. I suggest not mentioning the hypothesis related to anti-predatory behavior in the Abstract (line 60) and Conclusions (lines 1145 and 1146).
-Figure 2. Legend: species names should be in italics
- Figure 5. Legend:  C. cordovana and C. pagoda should be in italics
- Figure 7. Legend:  C. stelzneri striata should be in italics
- Figure 8. Legend:  C. stelzneri striata should be in italics
- Figure 10. Legend:  C. pagoda should be in italics
- Figures 12 and 15. Legend: Please specify that limits penis/epiphallus and epiphallus/flagellum are indicated. It would be helpful to indicate these limits also in figures 6 and 9.
-Figure 16. The axes are described in the text as Discriminant function1 and 2 and in Figure 16 as Canonical axe 1 and 2. Please change the axis names in Figure 16.


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: FROM MORPHOLOGY TO MOLECULES: A COMBINED SOURCE APPROACH TO UNTANGLE THE TAXONOMY OF CLESSINIA (GASTROPODA, ODONTOSTOMIDAE), ENDEMIC LAND SNAILS FROM THE DRY CHACO ECOREGION
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall summary: You have generated interesting data sets for shell, periostracum, reproductive anatomy and DNA sequences toward your stated objective “to revise the species of the genus Clessinia, under a morphological, geometric morphometrics and molecular combined approach”. Three taxa are subject to morphometric analysis and seven to molecular analysis with 16S and COI (twelve with additional sequences from GenBank for COI.)

Basic reporting

The paper does not follow a standard structure in that the results start with“Systematic accounts”, yet the classification adopted should be a conclusion of the paper, not a result. The placement of the Systematic accounts gives the appearance that the names used for the taxa were decided a priori rather than being determined by the analyses. I recommend that the Systematic accounts be moved to an Appendix. The description of the ecoregions within it (starting at line 363) might be moved to the introduction (or results if the information in relation to snails is novel). The information on “Taxonomic history of the genus” (lines 127 to 170, but not 171-175) in the introduction should also be moved the Appendix. This information is important for getting the priority of names of taxonomic entities right, but it distracts from the main focus of the paper: determining what entities should be recognized.

You give explicit results for Morphometrics and for Sequence Data, but not for periostracal or anatomical characters. The abstract emphasizes that “the importance of the periostracal ornamentation for species identification needed to be tested”, so stating these results clearly is necessary. Periostracum and reproductive anatomy are described in the Systematic accounts, but a summary of the findings is not presented until the Discussion. Both character sets distinguish striata from stelzneri: “in C. stelzneri striata the periostracal hairs are absent and the spiral rows are more scatter” (lines 997-998). and “the penis in C. cordovana and C. stelzneri striata shows a short, thin, penial sheath overlapping part of the penial distal portion. This sheath was not observed in C. stelzneri stelzneri” (lines 1006-1008).

The literature cited and background information are thorough, except that you do not address what species concept(s) you are using, and what criteria you use to distinguish species from subspecies. The distribution map in Figure 2 shows that the geographic ranges of stelzneri and striata overlap, so under a standard geographic subspecies concept, the rank of subspecies for striata is disproven. Either C. striata is a synonym of C. stelzneri, or it is a full species (or the distribution map is incorrect).

Background information on Odontostomidae is given in the first two paragraphs of the Discussion. This should be moved into the Introduction. The discussion also contains a considerable amount of information on the periostracum (lines 1062 to 1101) some of which could be moved to the Introduction.

Another area in which background information could be improved for the general reader is clearly definition of terms relating to Chaco. You use “Dry Chaco” as the broadest term for the ecoregion, with “Arid Chaco”, “Semiarid Chaco”, and “Chaco Serrano” (lines 383-384) as sub-ecoregions. In the caption to Fig. 2, “Arid Chaco” is apparently given as “Chaco”. Since some sources use “Chaco” and “Arid Chaco” as two separate ecoregions (e.g. https://www.worldwildlife.org/ecoregions/nt0701), this is confusing. “Espinal” and “Yungas” are also distinct ecoregions, but that isn’t stated in the figure caption. The colors are explained in Fig 2A. If the dark brown in Fig. 2B refers to the same region as in Fig. 2A, the key to colors should be at the level of the figure, not the subfigure.

The results heading of the abstract states “We found that species of Clessinia are endemic to the Chaco Serrano sub-ecoregion that is restricted to small patches within the Dry Chaco area. If that is actually a result of the paper, rather than background information, it needs to be brought out more clearly. Also, it needs evaluation to see if it is an overgeneralization. Figure 2 shows one site for striata is in Semiarid Chaco (west to Totoral) rather than Chaco Serrano, and some sites for each of the other taxa in “Chaco”, not Chaco Serrano.

In general the writing is unambiguous, but there is some non-standard English, for example use of “posterior” to mean “subsequent”. I provide some suggestions under “General comments” below.
Experimental design: The general idea of the study is sound, taking several lines of evidence and combining them to see what set of taxa is best supported. However, the methods do not provide a decision criterion—how to determine what taxa to recognize when the data sets contradict each other. In this case periostracum, anatomy, morphometrics all support more species than does ABGD. I recommend as a starting point Schlick-Steiner et al. (2010 Integrative Taxonomy: A multisource approach to exploring biodiversity. Annual Review of Entomology 55:421-438 (https://doi.org/10.1146/annurev-ento-112408-085432).

You state (line 274) that “Phylogenetic analyses were performed using Neighbour-Joining (NJ), and Bayesian inference (BI)”. Neighbor joining is a phenetic method, not a phylogenetic method. It doesn’t incorporate a model of evolution, so it is not appropriate for this kind of study. Apparently it gave the same topology as the Bayesian analysis, since bootstrap values for NJ are mapped onto the Bayesian tree, but this is not stated. It would be more appropriate to do parsimony or likelihood analysis as alternatives to Bayesian in exploring the sequence data. See this discussion on ResearchGate https://www.researchgate.net/post/Neighbor_joining_or_maximum_likelihood

Only mitochondrial genes were used for the phylogenetic analysis. A nuclear gene should be added as an independent marker. Mitochondrial genes may not yield phylogenies consistent with species relationships because of introgression. There is evidence that this has occurred in Clessinia. In the phylogenetic trees of Breure & Romero (2012), whom you cite, C. cordovana and C. stelzneri grouped with Spixia popana in the phylogram (fig. 7) based on the mitochondrial gene COI, but with only nuclear genes, they grouped with S. tucamanensis instead (figs. 5-6). Your results are more similar to their figure 7, showing the need to add a nuclear gene to the study.

Another problem with the phylogenetic analysis is that only a single outgroup was used. This makes the outgroup a long branch; including several outgroups would give a better assessment of polarity of characters.

Barcode distances were calculated based on only two or three specimens per species, but 10 per species is usually recommended (e.g., https://www.ncbi.nlm.nih.gov/pmc/articles/PMC2775153/). There may not have been enough data for a reliable determination of a barcode gap since there were few intraspecific comparisons and each putative species came from only one or two locations. Also,it is not clear how the histogram in Fig. 20A was compiled. It shows only 2 genetic distance values between 0.01 and 0.02, but Table 4 show 8 such values. The stated genetic distances between C. stelzneri stelzneri and C. stelzneri striata “1.1 to 1.8%” (lines 1014-1015) are too low; this is the distance for 16S (Table 3), but for COI, the barcode gene, distances are 1.3 to 3.9% (Table 4; note that C. s. stelzneri are IDs 16, 17 and 21 in this table). The higher end of the range is certainly consistent with species rank in many barcoding studies.

For the morphometric part of the study you state that the points “are homologous in all individuals in the analysis” (line 230), however, many of the landmarks on the spire are not true homologues. If individuals have different numbers of whorls, then you might be comparing, for example, whorl 6 to whorl 7.

It appears that points were determined differently between the discriminant analysis and the canonical variate analysis. In the former, height of aperture (Hap, Fig. 1E) was measured from the top of the aperture to the point on the lip directly below it on the shell axis. Diameter of aperture (Dap) was measured orthogonal to Hap, from the left most point of the inner lip to the intercept with the outer lip. However, these values are better determined by measuring between tangent lines parallel or perpendicular to the shell axis, as was done with minor diameter (dm, fig. 1D). The points to use for the tangents are shown in Fig. 1G, LM 10 to LM 8 for Hap and LM9 to LM7 for Dap.

In Fig 1C, diameter of spire (DS) is shown measured from whorl to suture instead of whorl to whorl. In Fig, 1A, the lines showing how the measurements were made are displaced from the figure, down and to the right.

Given that both of the morphometric analyses did fully separate the 3 taxa involved, these points about measurement may be of minor concern. However, all of the measured snails appear to have come from single populations (judging from the first table in supplemental data) in which case some of the differences could have been ecophenotypic. Broader geographic inclusion of individuals in the morphometric analysis would give a stronger assessment if the putative taxa are morphometrically distinct.
Validity of the findings: You don’t make it clear why only three species are subject to morphometric analysis, whereas twelve are in the molecular analysis. I think this is because the current taxonomic position of both Clessinia stelzneri and striata is as subspecies of Clessinia cordovana, which is not stated in the manuscript. Parodiz’s striata has never been treated as a subspecies of stelzneri (see chresonymy at line 574); Clessinia stelzneri striata is actually new combination introduced in the manuscript. Also, it is not the case as stated on lines 504 and 987 that Breure (1974) elevated stelzneri to full species status. He classified it on pages 110 and 113 as C. cordovana stelzneri. His mention of C. stelzneri cordovana (p. 123) is an error. His listing of Clessinia stelzneri on p. 124 is intended to refer to the original description, and does not indicate his own taxonomic placement. Breure & Romero (2012) treated the taxon as C. cordovana stelzneri. It seems unlikely that Neubert & Janssen, 2004 (line 504) used stelzneri as a full species, as their work is a type catalogue. This leaves Cuezzo et al. (2013), who did rank it as a full species, but this appears to be a misinterpretation of Breure (1974).

This all works to your benefit. As it is, the manuscript appears merely to verify the status quo, confirming two species and one subspecies. But actually, you have confirmed that stelzneri should be ranked as a full species as first named, and proposed that striata be a subspecies of stelzneri rather than of cordovana. I do not think you should take the latter action, however, because striata has geographic overlap with stelzneri, which precludes subspecies rank. Instead I think you should raise striata to full species status.

Your morphological and morphometric data sets each support full species status for all of the entities they include. Your conclusions, however, consider only the ABGD analysis, which is based solely on barcode gap, to suggest that C. s. stelzneri, C. s. striata and Spixia popana are conspecific. I do not think the results of the ABGD analysis are supported by the weight of your data. A more thorough analysis in the context of integrative taxonomy is needed, and I provide some suggestions toward that end below.

Puillandre et al. (2012), whom you cite, state “ABGD is fast, simple method to split a sequence alignment data set into candidate species that should be complemented with other evidence in an integrative taxonomic approach.” Give that all of your other data sets support full species status for striata, and the small sample size and lack of nuclear genes cast doubt on the ABGD, it seems that full species status for all the taxa considered should be the preferred conclusion. Low genetic distance between of some species might reflect recent speciation, or be a symptom of some of the methodological problems indicated.

Your data support the synonymy of Spixia Pilsbry & Vanatta with Clessinia Doering, 1875. If that is correct, Clessinia striata (Parodiz, 1939), whether ranked as a subspecies or a species, is preoccupied by Pupa striata Spix, 1827, the type species of Spixia, and needs a new name. this gives you the opportunity to name a new species with a new type series, a clear type locality, and a DNA sequenced holotype, rather than merely introduce a replacement name for striata.

The suggestion that the periostracal hairs function in camouflage should be identified as speculation. Another potential function could be to attract moisture. You might also consider in explaining periostracal function, why striata lacks periostracal hairs.
Additional comments: Title: remove the author and year of the genus. They are cited in the body of the paper so they don’t need to be in the title, since the paper is not about the date of publication. It might be worth adding “Argentina” to the title.

Line 31: change “conform” to “comprise”.

Line 32: change “scarcely” which is a bit colloquial, to “rarely”.

Line 34 and 88: say “rare endemic” rather than “endemic rare”.

Line 86: delete “Even,”.

Line 92: “during the last decade” This cites a study from 2009, which would seem then to refer to two decades ago, not the immediately past decade.

Line 99: “Doering 1874 [1875]”. This is a confusing form of reference. In the running text and references cited, the correct date under the International Code of Zoological Nomenclature should be given (1875). Under the heading for the taxon, more detail can be given on the dates of publication if needed. The stated versus true dates of publication can also be stated in brackets after the entry in the References Cited. This applies to references to “Doering 1875 [1877]”.

Line 103-105: Change “The distribution area of Clessinia is highly overlapped with species of Spixia Pilsbry & Vanatta, 1898, and in less proportion with Plagiodontes” to “The distribution area of Clessinia is overlaps largely that of Spixia Pilsbry & Vanatta, 1898, and to a lesser degree with that of Plagiodontes.”

Line 107: change “the doubt” to “doubt”.

Line 123-124: delete “on the basis of our new molecular study”; new evidence is already referenced at the start of the sentence.

Line 141: change ‘who read it from a handwritten label wrote” to “based on a label written”

Line 152: change “which name-bearing type is” to “typified by”.

Line 158-159 “following years”. Grammatically this means years after Breure & Miquel (2012), but the following paragraph refers to earlier events.

Line 160: change “Posterior” to “Later” or “Subsequent”.

Line 179: state where voucher specimens for the morphological and molecular studies are deposited, IBN and/or IFML (from line 301), and their catalogue numbers.

Line 180-184 “Hand collection…”. This should have its own heading, “Collecting and Preservation” rather than being under “Morphological Studies”, since the work also supported the molecular studies.

Line 181: snails rather than areas are “xerophilic”.

Line 183-184: “Fixation”, “fixed”. Alcohol is a preservative not a fixative.

Line 183: “alcohol 96%”, alcohol 75%; say “96% alcohol” and “75% alcohol; also state what kind of alcohol, presumably ethanol (mentioned on line 247).

Line 185: delete “and studying them”.

Line 186: change “where” to “were”.

Line 201: change “plain” to “plane”.

Line 203-24: “The number of whorls was calculated following Kerney & Cameron (1979)”. Number of whorls shouldn’t be under the heading for linear morphometrics as it wasn’t used in that analysis (Table 2).

Line 205-206:  “Measurements of type material of each species, is recorded in the species description…” This also doesn’t belong under the heading for linear morphmetrics.

Line 206: change “minimum” to “minimum”.

Line 232: change “digitalized” to “digitized”.

Line 298: change “punctual” to “point”.

Line 328: Technically what is labeled here as “Diagnosis” is a “Definition”; see the glossary of the ICZN. The diagnosis is the direct comparison to other taxa that follows (line 336-354).

Line 328: change “turriteliform” to turritelliform”.

Line 349: change “Type” to “type”.

Line 351: change “teeth less” to “toothless”.

Line 506: also list Breure & Romero (2012) for this combination.

Line 857 and 881: change “discriminate” to “discriminated”.

Line 906: change “none allometric” to “non-allometric”.

Line 912: change “with the detached of aperture respect to body whorl” to “to detachment of the aperture”.

Line 919: change “all two” to “both”.

Line 922-923: “Spixia cuezzoae clustered with specimens of Clessinia pagoda”—so did Spixia holmbergi.

Line 924-925: change “COI- based dataset” to “larger COI dataset including sequences from GenBank.”

Line 926: change “well supported” to “well-supported”.

Line 929: “tri-modal”. Fig. 20A doesn’t have enough structure to say it is tri-modal.

Line 940: change “Pulmonate” to “pulmonate”.

Line 963: change “differencing” to “differentiating”.

Line 978-979: “Nevertheless, morphometric information alone did not add precise information respect to the assignment of all specimens”. This is not true, the discriminant analysis achieved 100% success (line 887).

Line 985: change “Posteriorly” to “Subsequently”

Line 985-986: “C. stelzneri was elevated again to species (Breure, 1974).” No, Breure 1974 said “status: C. cordovana stelzneri)”, p. 110 and 113. Breure & Romero (2012) also treated stelzneri as a subspecies of C. cordovana.

Line 1102: change “By last” to “Finally” or delete it.

Line 1103: delete ‘Based on morphological evidence, current”.

Line 1104-1105, change ‘a detached shell body whorl aperture” to “the aperture detached from the body whorl”.

Line 1116: change “from” to “to”.

Line 1117: change “formed by” to “contains”.

Line 1118-1119: change “only known molecular sequences for four species (Breure & Romero, 2012), plus two new other added in the present study.” to “DNA sequences are known for only six species, including two added by the present study”.

Supplementary data
Linear measurements:

1)	Worksheet labelled C. cordovana has data on three taxa, not only C. cordovana.
2)	In Column A, delete “VENTRAL” since both lateral and ventral data are given.
3)	Delete extra worksheets

Field work permision in Catamarca
This was submitted as a “rar” file, which I don’t have the software to open. I recommend it be converted to something more standard, like pdf.

“Lateral links” and “Ventral links for geometric morphometrics”
The purpose of these files is not stated; a description should be added.

GenBank numbers
This file can be deleted since GenBank numbers are given in Table 1 in the manuscript.


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

Input:
Title: FROM MORPHOLOGY TO MOLECULES: A COMBINED SOURCE APPROACH TO UNTANGLE THE TAXONOMY OF CLESSINIA (GASTROPODA, ODONTOSTOMIDAE), ENDEMIC LAND SNAILS FROM THE DRY CHACO ECOREGION
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have revised the manuscript extensively in response to reviewers comments, improving the logical flow, and making the background information clearer, for example, refining the discussion of ecoregions and redrafting map figures so that terms are used in a consistent way through the manuscript and distributions are consistent with the terminology.
Experimental design: The authors in their rebuttal show that they have carefully considered their experimental design. They have not accept all of the reviewers’ suggestions, for example stating, “Although we used a multiple source of information we do not support the Integrative Taxonomy approach”. They cite appropriate literature in rebuttal to show that they are familiar with the debate. They have improved the experimental design by adding genetic data from a nuclear gene and morphometric data on individuals from more populations. As a result, they give a more balanced evaluation of their data, and have revised some of their conclusions.
Validity of the findings: The most significant change is recognition of all the taxa at species rank, rather than ranking one as a subspecies. That taxon, Clessinia tulembensis sp. nov. (as Clessinia stelzneri striata in the first submission) will probably be the main point of controversy in the manuscript. I agree with the authors that the taxon deserves species rank, but I think they can go farther in defending their decision.

Clessinia tulumbensis is genetically quite similar to C. stelzneri, and the phylogenetic analysis shows C. stelzneri as paraphyletic with respect to C. tulumbensis (Figures 3 and 4), which is not noted in the discussion. Paraphyly is not problematic--species unlike higher taxa are not required to be monophyletic in a phylogenetic classification—but it does show something interesting about the direction of evolution. Also, the authors describe the morphological differences between these taxa, but do not state that they have overlapping distributions as show in fig. 5D. These species are apparently sympatric, if  not syntopic, without morphological intergrades. That should be part of the argument for giving full species status to C. tulumbensis. A similar case of snails with strong morphological difference but little genetic difference because of recent divergence was published by Uit de Weerd and Velázquez (2017).

Uit de Weerd, D. R. and A. F. Velázquez. 2017. Pinning down Tenuistemma (Pulmonata: Urocoptidae): local evolution of an extreme shell type. Biological Journal of the Linnean Society 121: 741–752, doi 10.1093/biolinnean/blx041.
Additional comments: Custom Checks requested by PeerJ
•	DNA data: The authors have an appropriate statement of deposition of data in GenBank and cite GenBank numbers for sequences by taxon in Table 2. The data cannot yet be accessed on GenBank, presumably because the authors have requested it not be released until publication of the corresponding manuscript.
•	Field study: The authors present appropriate permits for their work in supplementary documents.
•	New species: I agree that the taxon they describe is a new species, and the authors have included an the statement required statement in the manuscript  [As an ICZN commissioner, I have to say that this statement is unnecessary; give the ZooBank registration number to meet ICZN requirements. No explanation is needed

I am concerned, however, to ensure that the authors do not run afoul of ICZN Article 72.7:
“If an author proposes a new species-group name expressly as a replacement (a nomen novum) for an earlier available one, then the two names are objective synonyms; both the nominal taxa they denote have the same name-bearing type despite any simultaneous restriction or application of the new replacement name (nomen novum) to particular specimens or any contrary designation of type, or any different taxonomic usage of the new replacement name.”

The authors are describing a new species to include the taxon named Odontostomus cordovanus striatus Parodiz, 1939. That name is preoccupied by Pupa striata Spix, 1827. They do not intend to introduce a new replacement name, but rather to name a new species with its own type series, so that the species is defined based on live-collected material from which DNA sequences were obtained and the anatomy described. That is, the intent is that Parodiz’s taxon and their taxon will be subjective synonyms, not objective synonyms.

The authors state, however, “The former Clessinia cordovana striata (Parodiz, 1939) is here raised to species rank, renaming it as Clessinia tulumbensis sp. nov.” It is possible that someone could invoke ICZN Article 72.7 to say that there is a contrary designation of types. This challenge could fail because the authors say “sp. nov.” rather than “nom. nov.” but it seems better to prevent the challenge from occurring to begin with. The authors should say that although the Parodiz name is preoccupied, they are not replacing it, but naming a new species for the reasons noted above.

General comments
Most of the following are just suggestions to improve phrasing.
Line 56: change “suggest” to “suggests”.
Line 112 change “is overlaps” to “overlaps” [I think this was my error from the first review].
Line 116, change “stressed” to “exacerbated”.
Line 195 change “is” to “are” to agree with “limits”.
Line 199 change “stablished” to “established”.
Line 413: change “by any of both methods” to “by either method”.
Line 440: self reference “Cuezzo, Miranda, Vogler and Beltramino, 2018” isn’t needed; Spixia should be attributed to its original publication here along with citation any works that used Spixia in that sense. “New Synonymy” should be lower case.
Line 457: change “teeths” to “teeth”.
Line 465: “ranging its area of distribution to”—not sure what is meant here. Possibly replacing this phrase with “in” would work.
Line 479; delete comma.
Line 484: change ‘of extension” to “in extent”.
Line 513 and 584: delete the dash, these are citations of original descriptions.
Line 518: also mention type material of C. gracilis.
Line 578: change “with” to “as”.
Line 627: change “idem to” to “same as in”.
Line 644: delete “The distribution area of C. stelzneri is located in”.
Line 650: delete dash before Parodiz.
Line 653: also mention type material of O. cordovana striata since it is not an objective synonym.
Line 813-814: Recommend deleting “C. pagoda is a rare species, endemic to a restricted area in northwestern Córdoba.” This distribution information does not contribute anything relative to the first sentence, and “rare” contradicts the following sentence, which says “easily found”, which suggests the taxon can be locally common.
Line 819: change “adheres” to “adhere”.
Line 823: delete “immerse”.
Line 848: change “rows” to row”. It’s not clear what is meant by, “Only one type of spiral rows present, some of them without spines intercalated with the ones bearing spines.” If some have spines and some don’t isn’t that two types of spiral rows?
Line 891: change ‘floor” to “ground”?
Line 902: change “the genera/species” to “taxonomic”.
Line 903: change “provides” to “provide” and “its” to “their”.
Line 906: change “this” to “the”.
Line 916: Periostracum doesn’t need definition here as it’s already been used dozens of times.
Line 927: change “dryer” to “drier”.
953-997: break this into two paragraphs.
Line 972: change “The same than” to “As”.
Fig. 2: a different green is used to the text for C. stelzneri than for the symbol.
Fig. 17B. The B is hard to see, maybe change to white?


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: DENSITY-DEPENDENT CHANGES IN THE DISTRIBUTION OF SOUTHERN RIGHT WHALES (EUBALAENA AUSTRALIS) IN THE BREEDING GROUND PENINSULA VALDÉS
Review round: 1
Reviewer: 1

Output:
Basic reporting: This paper is reporting on the density-dependent changes in the distribution of southern right whales in the breeding round Peninsula Valdes.  The authors provide good data on a population of whales that needs more information, particularly as things are changing – this kind of monitoring is vital.  The overall idea of the paper comes across, but there needs to be more work done on the structure and flow of the paper to increase clarity and readability.  The basic reporting here is good, but needs improvement for publication.  There is some inconsistency with numbers (using commas vs. periods), and quite a few grammatical/spelling errors.  Some of the sentences are confusing and need to be reworded for clarity and understanding.  The intro and background do give context, however I think much can be improved here.  Improvements can be made to sentence/paragraph structure, clarity of details and providing more detail/context in the introduction, which can then be discussed further in the discussion.  In particular the authors should make a clear case as to why their study needed to be done, as much of the references are recent, and seem to cover much of the same information they are showing.  I believe there is some overlap, but that this study was needed to explicitly (and numerically) show the changes occurring, but the authors need to make sure they frame this correctly throughout the paper in relation to all the other studies done on this population.  See general comments for specific details.
Figures are relevant and show the data clearly, but need improvement on some captions and data labels.
Experimental design: This paper seems in the scope of the PeerJ journal.  Overall the methods are good, but more details/increased clarity is needed in some spots.  The research question is defined, however I think it can be made clearer (in relation to what was stated above in the basic reporting section) – in particular how does it fill an identified knowledge gap with all the other recent research being referenced. See general comments for specific details.
Validity of the findings: The authors provide valid results related to the question being asked, which is a valid question to investigate.  Overall the conclusions are well stated and link to the original research question, however restructuring is needed in the discussion to more clearly define speculation/conclusions and providing support for each.  I cannot say whether the statistics are completely appropriate or not. See general comments for specific details.
Additional comments: Abstract
Line 17: Southern Right Whales are (not is)
Line 18-21: combine this two sentences – there is no need to say, ‘as a consequence of population increase’ twice, since it is the same reason for both results. (so …. were recorded, and distribution and density in the core area are suspected.
Line 23: Please state what the 4 periods were.
Line 25: capitalize the.  Can you give a little more results here – there are some interesting things you bring up in the discussion part, but you can’t get any of that from this short results section.
Introduction
Line 31: object or subject?
Line 31: I would use regular numbers here, unless this is a formatting issue for the journal.  Not everyone can read roman numerals this large.
Line 46: There are a lot of years being thrown around here – when is 8% at that time? The 80s?
Line 47-53: It is a little confusing how the Cooke and Crespo studies are related (or not).  They seem to overlap in time, but are showing the same thing?  Are all the numbers population increases/decreases – and if so, then having the sentence line 49-50 in the middle is confusing because it makes it seem like the next sentences about the Crespo study are about that maximum number of whales in Aug/Sept vs. the population increases like the Cooke studies.  Please rework this section to make it more clear chronologically and in what each study was showing relating to the point you are trying to make (which I think is that the population increases were decreasing in more recent years).
Line 57: Please add a sentence in here describing the types of all class groups involved.
Line 59-60: This sentence is not clear – where are the solitary and breeding groups?
Line 63: add population before increase – so it is a decrease in the rate of population increase (makes this more clear).
Line 68: supporting
Line 70: remove the (so in sourthern Brazil).

Methods
Line 89: remove on of the ‘on the’
Line 91: Please explain more the Breeding groups category – why n-1 males?
Line 95: on the Beaufort scale.
Line 96: What database? Please describe your custom database (and what software it runs on, i.e. is a access based, etc?)
Line 99: This is the info that would be helpful in the abstract (similar number of flights being the reason for clumping).
Line 104: Remove ‘later the coast of’  Start with The surveyed coast was divided….
Line 104-111: Is this density different than the one in line 102-103? Please clarify. Also, it is unclear what your calculation is; you divided the number of whales be what?  You just explain the weighted part – is that what you divided it by?  Perhaps an example calculation would be helpful here.
Line 112: This seems like results, not methods – didn’t the data show you what was high vs. low density? If not, then please explain more here what these are and how they were determined.   I think perhaps you did get this from the data, if so then please explain this here.  I.e. based on the data we determined high density to be xxx (or more) and low density areas to be xxx (or less) and used Mann-Whitney U tests to determine if the differences between these areas were statistically significant.

Results
Line 131-132: Put a periods after (segment 97 and 98), the rest of the sentence is redundant since you stated this in the beginning.
Line 132: Where and what time was this maximum mean density found?
Line 148: For the Other groups there was (not the was)
Line 151: only (not obly)
Line 126-154: For those not familiar with the area the results section is not clear, it is hard to follow with all the names and segment numbers.  I would suggest subtitling two sections under the Results, 1. High density areas, 2. Low density areas – that will make which overall areas you are talking about. I would suggest that naming them isn’t needed in the text here, perhaps giving them numbers on the figure would help, then you can just put the numbers here.  I would also like to see a clearer layout of how many high vs. low density zones there are, and how many showed increase or decrease (i.e. did all high density areas show the same trend?). Although I get the idea here, I think this section can be reworked to be clearer and have more information included.

Discussion
Line 159: This is an interesting idea, and the fact that you have a number for the threshold – but that wasn’t made clear in the results.  Was it at that number when you started seeing shifts in the m/c vs other groups increase/decreasing in particular areas? If so, lay that out in the results more clearly, then discuss it here.
Line 161 – I think it should be 15.87 (not 15,87)
Line 162: description of what processes?  This sentence is confusing, and what average are you using, the 15.87 or the 3?
Line 163: These kinds of changes, also southern right whales (not whale).  This sentence is also confusing – what kinds of changes? The decreases in other groups you are documenting? Or the increases seen in Aug/Sept?
Also in the rest of the paper Southern Right Whale is capitalized, but here and afterwards it is not. Please be consistent throughout the paper.
Line 165: Rowntree et al. proposed (not propose).
Line 168: several factors such as…
Line 170: I would hesitate linking density to socially so directly.  Although they can be linked, they aren’t always, as you could have density effects in relation to foraging that would not necessarily have a social component (there is just how much food there is to go around, regardless of how the animals may interact).  I think that there very well may be a social component, but the data related here cannot state a clear link, so I would caution the authors to suggest this, but not state as fact.
Line 175-76: the sentence is not clear – if they are the same activities, how are they new interactions?  Please state what the new interactions are, and who is doing them more clearly.  Then this is where you can suggest a little more strongly that social causes may be a large part of the distribution shift, since there is other evidence besides just the density shifts you show. *also after getting to the end I see you bring more evidence… I suggest you put this statement toward the end, after you have shown other support.  So start here with suggesting this might be a cause, then go through and discuss why based on your results and other studies in the literature.
Line 181: This is the info you want in the results, so you can reference again here.
Line 185: not only was there….
Line 187: remove ‘in the second period’ – this is redundant since you started the beginning of the sentence talking about the next period, after the first.
Line 199: groups move (remove are a).  Also this sentence is a good one, and may be useful in the introduction supporting the need for the current study to document the actual density changes, and see if they follow the same trend in this area.  I would perhaps also note in the text where the Svendsen study was done – to show that if it was done in another area, that now your study will investigate this trend in your study area; and if it was done in the same area, you should explain why your study was needed, as it sounds like similar information was presented in that study).
Line 200: mechanism was
Line 202-204: How is this different than the red deer you just talked about?  You don’t talk about abandonment of areas in any species, there is no need for this sentence in relation to fission/fusion societies in particular. I would remove it, but if you want to keep it then please state more clearly other examples of different populations that increase by abandonment, along with others that support your idea about fission/fusion being different.
I would also move the roe deer example up after the red deer… put them together since your mechanism is both increasing spatial distance and the changes in habitat use that differ by group type. Then show how that happened in your study, and in other studies you have mentioned.  This will give a better flow to the paragraph and a clearer discussion.
Line 205: remove of (so , new matrilineal lines). Also change to ‘establish new breeding areas in time’.
Line 206: remove the from the roe deer – it makes is sound like you have talked about the roe deer before when you have not.
Line 210 remove the comma
Line 211: the groups used the habitat differently? That is an interesting point that should be discussed more and probably brought up in the introduction, again as support for why you are doing your study.
Line 215- 216: again info that would be good as background in the introduction.

Conclusion
Line 221: One proposed mechanism is…
Line 223: well
Line 225: What is ancient habitat?  I thought the new areas were new… are they moving into new areas or recolonizing older areas?  This should be stated more clearly in the introduction.

Figures
Figure captions should all have punctuation.
Figure 1: is it 0.05 or 0,05? Be consistent in the manuscript.  Also what is the unit for density here – whale/km or whale/km2?  Please state it clearly in the graph. I would also highlight the high and low density zones here if possible (or at the very least the 2 high density zones).
Figure 3: I would remove the last part of the sentence ‘without discriminating the group type’ – you did discriminate the group type in the graph, and have them all combined.
Figure 4 and 5: the should be capitalized.


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: DENSITY-DEPENDENT CHANGES IN THE DISTRIBUTION OF SOUTHERN RIGHT WHALES (EUBALAENA AUSTRALIS) IN THE BREEDING GROUND PENINSULA VALDÉS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The introduction section is well written and provides a good overview of the population being studied. As the article brings a new concept which has never been demonstrated for baleen whales in breeding areas, I believe that an overview of the topic at the end of the introduction section is crucial. The authors make reference to “Matthysen E. 2005. Density-dependent dispersal in birds and mammals. Ecography 28:403” but very superficially.

Along the text (see the pdf and the word files) I have made suggestions to improve the clarity and the grammar. I believe that a table would be a good support to summarise the periods and the data being used for the reader. I provided few comments to the figure 1, in which the areas of higher density could be illustrated to guide the readers.
Experimental design: -I suggest the adoption of another term for the categories of groups being compared: Mother-calf pairs and groups without calves, which includes solitary and breeding groups. What about dyads or trios? Are these group categories observed in the area?
-In the methods section, it is not clear for the reader if the areas of higher and lower density were defined prior or identified during data analysis.
- The average of mother-calf pairs never reaches 3 whales per km2. The density of all groups combined is greater than 3 in the first period in the segments that correspond to El Doradillo area. In the discussion section the authors state: “This response includes the movement of Solitary Individuals and Breeding Groups (Other Groups) to adjacent areas when the average density in the area is close to 3 whales per km2.” and: “During the peak of the season, as much as 15,87 whales per km2 can be found in the El Doradillo area but the description of the process can be better viewed using the average.”
Why is 3 whales per km the threshold? It is really not clear how the threshold was established.

-Was it the aim of the article to establish the threshold? If yes, the methods to define it have to be better described. If the aim was only to describe the probable process that is guiding habitat use patterns, is the value really necessary? If at the peak of the season density can be five times higher in high-density areas, is the number that matters, or the process? If it is the number, again, the method to identify it is not clear. I think that it is extremely important here that the assumptions made during the data analysis be clearly stated. You have pooled all observations together to get a density for a period. Why? Why haven't you calculated the density by month or period within a year and after made an average to take your n into consideration (number of flights). These points must be clear in your methods and discussed. If your goal was to characterise the spatial process, then, the discussion (mainly) must be reviewed in consequence.
Validity of the findings: The article uses a large data set to demonstrate an ongoing process with important consequences on the species habitat use patterns. To my knowledge, a density-dependent process has never been demonstrated for baleen whales in breeding areas. The methods need to be better presented and the results better discussed in order to allow the reader to replicate the analysis and to validate the analysis that was made.

The authors make often reference to the article of Crespo et al which is in press. I assume that the same data set is used in both and different aspects are presented in each. However, in different points of the discussion of the present article, it is not clear if the concept of density-dependence is being proposed here, or by both. The same argument stands for the article of Arias et al.
Additional comments: Check the spelling of all locations. Doradillo or El Doradillo?
I have made all my comments along the text. I started by the pdf and moved to the word file, I am sorry for that!


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 DIVERSITY AND COMMUNITY IN QULA FROM THE QINGHAI–TIBETAN PLATEAU IN CHINA
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript reports phylogenetic and functional diversity of microbial communities in Qula from five geographically distinct regions in China. The authors conclude that microbial phylogenetic and functional diversity varied by geographic region. In addition, the authors suggest that their results indicate that traditionally made Qula may be unsafe to consume following long storage time and/or poor packaging (e.g. see lines 252-253). The authors make a compelling case for the importance of understanding microbial dynamics in Qula. However, there are major issues including:

1)	A potentially inaccurate description of the methods (i.e. was this a metagenomics study or not? See Experimental Design #1 & 2).

2)	The methodology is not clearly defined and as a result it is unclear what the “triplicate” Qula samples represent (e.g. are samples #1-3 from one/multiple Qula/yak/producers? See Experimental Design #3).

3)	There is inadequate background information to contextualize the results (e.g. how and why (be specific) might Qula microbial communities differ as a function of the five distinct geographic locations? See Basic Reporting #1; Experimental Design #3, & Validity of the Findings #1).

4)	There is insufficient data reported in the manuscript to support the authors conclusions (e.g. what evidence is there to suggest that poor packaging and long storage times lead to unsafe Qula? See Validity of the Findings #2).

5)	Other issues regarding the text and figures/tables (see Basic Reporting #2 & 3), as well as the validity of the findings (see Validity of the Findings #3).

BASIC REPORTING
1.	Literature references, sufficient field background/ context provided:
-	A major issue with the current study is the lack of background information on the five geographic locations of Qula collection (i.e. Yunnan, Xizang, Qinghai, Gansu, and Sichuan). In the absence of any measured and/or discussed differences based on geographic location, it is unclear why and how Qula microbial communities might vary with location. Simply suggesting that geographic location, and thus environmental factors, may have impacted the microbial communities is too vague to be insightful. A discussion of how “elevation, climate, temperature, oxygen level, and atmospheric pressure” (lines 226-227) varied across the five locations would strengthen this manuscript.
-	The literature discussion in the Introduction is too brief and fails to provide a comprehensive summary of previous research. For example, Zhang et al. (2015) used rRNA sequencing to study bacterial communities as a function of Qula development, suggesting that more than just “numbers of microbes” (line 47) was assessed prior to the current study. I believe the authors are trying to distinguish between culture independent (current study), and culture dependent (e.g. Zhang et al. 2015) studies of Qula communities (compare lines 44-47 to 47-48). This is an important distinction that should be stated more clearly to maintain proper representation of previous work.

2.	Professional article structure, figs, tables:
The authors have organized the manuscript into professional and coherent sections and have made all raw data available in the SRA at the NCBI.

Figures and Figure Legends:
Fig 1: Ordering the legend to match the stacked rarefaction curves would enhance the readers ability to quickly line-up each curve with geographic location (just a suggestion).
Fig 2: There is no information in the text or figure legend suggesting that we should compare across the bars in the order in which they are connected. As a result, the extra color in the plot is ultimately confusing (e.g. I stared at the plot for a while trying to figure out what light pink indicated). Additionally, converting to a log-scale would enable visualization of the less abundant groups (i.e. currently cannot see Acidobacteria or Cyanobacteria).
Fig 3: See comments for Fig 2.
Fig 4: This is a complicated plot and requires a much more descriptive legend. Further, based on the 4 lines of text that references this figure (lines 170-174) it shows differences in bacterial OTUs between regions – how is this different from Fig 7?
Fig 5: What level of bacterial taxonomy is being compared? Need to include this in the legend.
Fig 6: Why does QH1 cluster with other QH samples in this figure, but with the XZ samples in the following dendrogram (Fig 7)?
Fig 8: This figure would be significantly more informative if there was some level of identification of the KO #’s. For example, organizing these into higher level classifications (e.g. amino acid metabolism) would help the reader to quickly assess what major metabolic differences are present in the geographically distinct communities. Again, QH1 is not clustering with the other QH samples, but with the XZ samples, and this should be addressed.
Fig 9: Though I am not familiar with network plots, Fig 9 is only referenced in lines 204-206 and it is not clear to me how this information informed the conclusions for this study. Could this figure be removed?

Tables and Table Legends:
Table 1: Might the Qula microbial communities differ based on the color of the grain? Yunnan had the lowest diversity and based on this table it seems that color of grain, rather than geographic location, may have influenced the Qula communities. How long have these Qula’s been stored (e.g. line 252)? How “badly” was the Qula packaged (e.g. line 253)? Do #1-3 (e.g. YN1 – YN3) represent triplicate samples collected from a single Qula purchased at each location? Or are samples #1-3 three different Qula’s bought from the same (different?) market(s) at each location? This table, as well as the text, require significantly more detail to understand the sampling methods employed.

3.	Clear and unambiguous, professional English used throughout:
I commend the authors for their clear and professional writing. However, there are multiple minor spacing and grammatical errors, as well as ambiguous portions of the text that need to be addressed – I have highlighted some of these here:

Line 20 – “and a total of 47 OTUs at different levels significantly differed…” what does this comparison mean if they are at different levels?
Line 21 – “The functional genes of the bacteria present in samples also indicated differences in bacterial communities between the samples…” this is misleading and needs to clearly state that functional genes were not directly assessed, but rather predicted based on phylogeny
Line 44, 44, 45, 53, 64, 77 (need to check throughout paper) – multiple locations throughout the text require a space to be inserted.
Minor grammatical errors including line 76 (‘wereas” should be were as), line 89 (“sequence” should be plural), line 112 (what does “respectively” refer to?), and line 131 (“bacterial and bacterial phylotypes”).
Line 49 – “;” should be removed
Line 63 – It is unclear what “five types” of Qula refers to. Are “types” equivalent to geographic location? If so, are samples #1-3 representative of triplicate samples from a single Qula? Or three different Qula’s purchased from each location? Other? This needs to be clearly stated in the methods.
Line 140-145 – This paragraph is confusing as it is unclear which samples exhibited significantly different species richness, and which did not. Additionally, it is not clear to me what “also” in line 144 refers to – geography, and what else?
Line 186 – Is “douchi” meant to be “Qula”?
Line 209 – “Obviously, the network…” The distinction between dominantly cooperative and non-cooperative interactions is not obvious to me. A brief introduction to network analysis would strengthen this section by providing the context required to assess these plots.
Line 227 – “Sun et al. 2010” should not be red
The first paragraph in the Discussion section suggests that Qula may be unsafe to consume because of the presence of pathogenic bacteria; however, the second paragraph suggests that the presence of “alcohol, lactic acid, acetic acid” producing bacteria may inhibit the growth of pathogenic bacteria. These contradictory speculations are never addressed simultaneously and as a result, the reader is left unsure whether Qula is unsafe or safe to consume. A more comprehensive and cohesive discussion of the study would strengthen this manuscript.
Experimental design: The research question - to assess “diversity of microbial communities in Qula from different regions in China” (line 12) – is well defined. In addition, this study contributes to a growing understanding of food ecology of Qula (line 274) through the use of culture-independent molecular techniques (e.g. line 55). However, there are major issues with the experimental design:

1.	A crucial distinction that needs to be addressed in future iterations of this manuscript is whether a metagenomics analysis was, or was not, conducted. Line 65 states that Qula samples were collected for “metagenomics DNA [analysis]”; however, the following sections suggest that primers were used to amplify 16S rRNA genes and that PICRUSt was used to infer metabolic function from phylogeny. My understanding is that isolating and sequencing 16S genes is not a metagenomics analysis. The use of “metagenomics” needs to be addressed throughout the manuscript.

2.	In the absence of a metagenomics analysis, a compelling case needs to be made for using phylogeny of Qula microbial communities to infer community metabolic function.

3.	The sampling method is not clearly defined. For example, it is not clear whether the 3 samples (#1-3) for each of the 5 geographic locations represent 3 different Qula made by different producers (and possibly 3 different Yak), 3 Qula produced from one producer (maybe one Yak), or whether the 3 samples are triplicate samples from one Qula. Without a clear understanding of the samples collected, it is difficult to assess whether the differences in microbial communities resulted from different source animals, producers of the Qula, environmental factors that may vary by geographic location, etc.
Validity of the findings: 1.	As stated in Basic Reporting #1 & Experimental Design #3, there is insufficient background information on the Qula samples to assess whether the microbial communities differed as a function of geography, grain type (i.e. white vs yellow), producer of the Qula, age of the Qula, packaging of the Qula, etc. If there is compelling evidence to suggest that the differences between samples are due to geography, a detailed discussion of why and how geography may alter Qula communities is needed.

2.	I have found no evidence in this manuscript to support the authors conclusion that “badly-packed Qula” and “long storage times” may increase the colonization of Qula by pathogenic bacteria. If data on these two storage methods was collected, it needs to be included.

3.	There is no discussion of the clustering of QH1 with the samples from XZ, for both the community and functional analyses. A discussion of why this sample might be less like other QH samples, and more like samples from XZ, is needed.
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 DIVERSITY AND COMMUNITY IN QULA FROM THE QINGHAI–TIBETAN PLATEAU IN CHINA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The writing needs substantial work for clarity and grammer. Please see details in attached review.
Experimental design: The presented objective does not match the analyses. The research objective is presented as an analysis of regional effects, but no metadata are included that would enable analysis of regional drivers. Substantial revision of analyses and additional data are needed if the paper is to be presented as a regional analysis. Otherwise, I think the data are still publishable but the paper needs to be revised to present a simpler goal (a basic description of the bacterial communities of Qula).

Statistical methods need some clarification.

Please see attached review.
Validity of the findings: Validity of findings depends on issues described above (writing, objectives, and statistics). In addition, the PICRUSt and network analyses need more thoughtful treatment. Please see attached review.
Additional comments: Please see attached review.


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 DIVERSITY AND COMMUNITY IN QULA FROM THE QINGHAI–TIBETAN PLATEAU IN CHINA
Review round: 3
Reviewer: 1

Output:
Basic reporting: 1. Literature references, sufficient field background/ context provided:
Reference to “elevation, climate, temperature, oxygen level, and atmospheric pressure” was removed and the authors provide a compelling discussion of the potential for yak breed, diet, and parity to impact differences in Qula microbial communities. In addition, they discuss the potential of house flaura, and storage time, to influence Qula microbial communities in the absence of starter inoculum.

- The authors have sufficiently addressed my original concern that the literature discussion in the Introduction was too brief and failed to provide a comprehensive summary of previous research.

2. Professional article structure, figs, tables:
Fig 1: This figure is not re-ordered in my copy of the manuscript...but again, this is not a huge deal.

Fig 2 & 3 (now Tables): were converted to tables and though these are easier to read than the original figures, I find it much easier to view changes in community composition in a stacked bar plot. The authors may consider including stacked bar plots of community composition in addition to the tables.

Fig 4 (now Fig 7): The authors updated the figure legend and the figure is now easier to follow.

Fig 5 (now Fig 3): The authors updated the figure legend to include the level of taxonomy.

Fig 6 (now Fig 4): QH1 has been highlighted throughout the results as not clustering with the other QH samples. However, “.family” needs to be updated.

Fig 8 (now Fig 6): The authors have updated this figure and it is now much easier to decipher broad changes in potential community function.

Tables and Table Legends:
- Lines [55-56] indicate the Qula samples were purchased directly from different sellers at local markets in five regions. I recommend explicitly stating that samples #1-3 are “not representative of triplicate samples from a single Qula” to make this completely unambiguous to the reader.

3. Clear and unambiguous, professional English used throughout:
- There are still grammatical errors and missing spaces in my copy of the manuscript.

- The authors provided a clear explanation of the Qula samples in their response to my review, however, I recommend explicitly stating under the Sample Collection section that "samples #1-3 are not representative of triplicate samples from a single Qula", but rather non-replicated samples "bought from different producers at each location".

- [Line 206] I very much appreciated the authors explanation of Fig 7 in their comments to my review; however, this is not addressed in the text and if it is not obvious to all readers, I would suggest updating the text and/or removing “obviously”.

- I commend the authors for updating the text throughout the manuscript to reflect the limitations of their study and the requirement for further experimentation to understand whether Qula is safe to consume.
Experimental design: The authors have done a nice job making clear that this was not a metagenomic study (it might be helpful to explicitly state this was 16S amplicon sequencing in the abstract). However, I would still recommend including a discussion of other studies/ motivation for using PiCRUST to assess metabolic potential of the communities.
Validity of the findings: The authors have added a well written and cited discussion of how microbial communities on Qula may be impacted by yak breed, diet, and parity, as well as house floura and storage times. In addition, the authors have updated their discussion to reflect the limitations of their study.
Additional comments: In case it's easier to read through, I have included a word document with my updated review in blue.


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 DIVERSITY AND COMMUNITY IN QULA FROM THE QINGHAI–TIBETAN PLATEAU IN CHINA
Review round: 3
Reviewer: 2

Output:
Basic reporting: Unable to evaluate. Revisions did not address my major concerns from the previous review.
Experimental design: Unable to evaluate. Revisions did not address my major concerns from the previous review.
Validity of the findings: Unable to evaluate. Revisions did not address my major concerns from the previous review.
Additional comments: The authors have not addressed any of my major concerns, therefore I cannot review the manuscript in its current form. My review was structured in two parts: The first part of the review described major problems with the paper, where I devoted a paragraph to each of the following: (1) overview, (2) Basic characterization versus regional analysis, (3) statistics, (4) issues with PICRUSt, (5) issues with network analysis, (6) writing. These are major, general issues not associated with any specific line number in the manuscript. The authors have not addressed any of the major points.

The second part of my review listed manuscript lines to which I had miscellaneous or specific questions.  The authors have responded to these, but given that the major revisions needed are not addressed at all it does not make sense for me to review these minor revisions.


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

Input:
Title: BACTERIAL DIVERSITY AND COMMUNITY IN QULA FROM THE QINGHAI–TIBETAN PLATEAU IN CHINA
Review round: 4
Reviewer: 1

Output:
Basic reporting: Please see general comments.
Experimental design: Please see general comments.
Validity of the findings: Please see general comments.
Additional comments: The authors have made substantial revisions to the manuscript, particularly the discussion, description of statistical analyses, and quality of the writing in general. I appreciate their hard work to improve the paper. Many of my concerns have been completely addressed. A few areas still need a little work. These are straightforward and I am confident that the authors can rectify them with minor additional revisions. I have outlined these below, with the history of communications regarding each point pasted in for context. My most recent comment in each case is annotated "Reviewer Response".
Note to the authors: please address all issues in the manuscript itself, not just in your response to me. Thank you.

Issue 1:
Initial Reviewer comment: What environmental factors differ between regions? How are they likely to affect the Qula microbiome?

Author Response:Thank you for your advice. The previous discussion was not proper and they were revised in the revised manuscript. In the production of Qula, no starter is used to inoculate unpasteurized yak milk, and naturally occurring microorganisms serve as the inoculums instead. Therefore, the process of fermentation is largely affected by the local ‘house flora’. Different environmental factors lead to different ‘house flora’. The five sampling locations have different local ‘house flora’, which may lead to significant differences in the microbial community between samples. These were included in the discussion (see lines 234-238 in the revised manuscript).

Reviewer response: This is interesting. Please provide a reference for the statement that different regions have different “house flora”.

Issue 2:
Initial Reviewer Comment: The study uses PICRUSt to predict the Qula functional genome.  With PICRUSt, the usefulness of the result depends on whether the PICRUSt database includes genome sequences of isolates that are closely related to the bacteria in the sample being studied. I recommend demonstrating the validity of the PICRUSt data in two ways. First, state if there is there a threshold (minimum percent identity between the sample 16S read and database hit) for a genome to be included in analyses. Second, report the proportion of the bacterial community in the sample is represented by PICRUSt data. (If the community is mostly made up of taxa that are rare in PICRUSt’s sequenced genomes, then most of the data acquired from PICRUSt will link to taxa that are relatively rare in the study sample, and therefore the overall PICRUSt data will not represent the community functional genetic profile.)

Author Response: Thank you for your advice. We use a ‘closed-reference’ OTU picking protocol, and the threshold of Picking OTUs for use in PICRUSt is 97% (see lines 106-107 in the revised manuscript). OTUs that a KEGG profile could not be retrieved constitute the fraction of unexplained taxonomic units (FTU) (Aßhauer et al., 2015), they were included in the tabe S1 (see lines 108-110 in the revised manuscript).

Reviewer Response: The manuscript states “The threshold of Picking OTUs for use in
PICRUSt is 97%.” (L. 106.) Please clarify: does this mean that every OTU in your study had 97% similarity with a sequenced genome in the PICRUSt database? (Other than the few that were in the FTU fraction, which was only about 10% of OTUs for most samples.)

Issue 3:
Initial Reviewer Comment: L 259 [line number from first draft]  “In the bacterial network, most of bacterial genera were positively associated with each other.”  I think the authors should discuss the possibility that this result is an artifact of relative abundance data. For example, if one very common taxon decreases in relative abundance, then several other taxa may increase in relative abundance simply because total relative abundance has to add up to 1. This problem is not unique to the current study – it is a problem with all relative abundance data – but because this study has little additional information to help determine the biological plausibility of the interactions it’s particularly important to acknowledge the possible artifact due to working with relative abundances.

Author Response: Thank you for your advice. Yes, the limitation is existed in the present bacterial network. In the further studies, the bacterial genera in Qula samples in different fermentation time or storage time will be used for network analysis.

Reviewer Response: I think the authors have misunderstood my comment. For a more detailed explanation, please see papers such as Gloor et al 2017 “Microbiome Datasets Are Compositional: And This Is Not Optional” in Frontiers in Microbiology). The important point is that you need to state, in the paper, the possibility that correlations among relative abundance in your data may be an artifact of compositional data, and may not mean anything regarding the ecology of the microbial communities at all.

Issue 4:
Initial Reviewer Comment: Throughout the paper, bacterial taxa are distinguished as being “dominant” or not dominant, but there is no definition of what it means to be dominant. How is the dominance status of an OTU determined? For examples, see L. 155-169. L. 193-198 gives a similar example with respect to predicted functional genes.

Author Response: Thank you for your advice. The dominant taxa has a relative abundance >1%.

Reviewer Response: This issue is still confusing in the manuscript. It does not seem like dominance is only based on a relative abundance of >1%. For example the abstract reads: “A total of six phyla were identified with relative abundance >1% in the samples, and Firmicutes and Proteobacteria were dominant.”

Issue 5:
Writing and grammar: The authors have improved the writing. However, there are still some typos and grammatical errors. E.g. line 34 (“dispersion of fresh yak”, should probably read “dispersion of fresh yak milk”), line 39 “molecularbiology” is not one word. These are only two examples. Please assess the whole manuscript once again for errors.


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 DIVERSITY AND COMMUNITY IN QULA FROM THE QINGHAI–TIBETAN PLATEAU IN CHINA
Review round: 5
Reviewer: 1

Output:
Basic reporting: Please see general comments.
Experimental design: Please see general comments.
Validity of the findings: Please see general comments.
Additional comments: The authors have put a lot of time into revising this manuscript. Though I did not receive a response from the reviewers for this last round of reviews, I have read through the manuscript and see that most of my suggestions have been adequately addressed. I am confident that with a few minor revisions they can address the remaining issues.

Writing and grammar:
There are still numerous lines throughout the manuscript that are missing spaces. E.g. line 76 and 80 “(…Caporaso, et al., 2012).Sequence…”; “…(Edgar, et al., 2011).Quality…”

Line 99: I believe “was” is meant to be “were” (“Differentially abundant features among the different samples was identified using…”

Line 108: I believe this sentence is missing a few words “OUT’s that a KEGG profile could not be retrieved constitute the fraction…” This could read ‘OTUs for which a KEGG profile…’

Line 114: I believe this sentence is meant to read “Spearman’s rank correlations between selected genera were calculated using the (insert name) R package…”

This is not a comprehensive list and I would encourage the authors to do a thorough review of the entire manuscript for errors such as these.

Citations
Are the citations in line 98 correct? They don’t refer to the adonis (PERMANOVA) or ANOSIM packages in R, and a quick ctrl-F doesn’t bring up either acronym in either paper.

Lines 279-281 are a bit misleading as, for example, Pavloudi et al. 2017 do not use PICRUST to predict microbial functional diversity, they use the R package Tax4Fun. I bring this up because it appears there may be differences in the quality of functional predictions based on environment (e.g. Iwai et al. 2015; DOI: 10.1371/journal.pone.0166104).


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 DIVERSITY AND COMMUNITY IN QULA FROM THE QINGHAI–TIBETAN PLATEAU IN CHINA
Review round: 5
Reviewer: 2

Output:
Basic reporting: Please see General Comments.
Experimental design: Please see General Comments.
Validity of the findings: Please see General Comments.
Additional comments: The authors have addressed all of my critiques. I thank them for their continued efforts revising this manuscript. I have no further concerns.


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: DRIVERS AND ASSEMBLIES OF SOIL EUKARYOTIC MICROBES AMONG DIFFERENT SOIL HABITAT TYPES IN A SEMI-ARID MOUNTAIN IN CHINA
Review round: 1
Reviewer: 1

Output:
Basic reporting: Basic Reporting
Introduction
Lines 42-45: this text is not clear
Lines 73-74: revise text, does not flow well from the text before
Line 80: revise the use of the connector However
Literature: about 40% of the articles cited are older than 2008. It is important to report newer and updated research reports
Materials and Methods
Lines 108-111: what is the purpose of this text? Is not connected with the rest of the paragraph
Line 124: regarding figure S1, are the authors of this article the creators of the image? Also, the legend description is poorly descriptive. Moreover, in the figure there are two soil depths shown and, in the methodology, only one is mentioned
Line 150: check xxtraction misspelling in legend for table S1
Line 155: check reference format
Results
Lines 184-185: revise the text regarding OTU, it is not clear and does not flow well
Line 193: regarding table 2, revise number of decimals reported. Be consistent on the number of decimals reported for each metric
Discussion
Line 263: check the use of the word however
Figures and Tables
Table 1: revise superscript in data units
Table 2: use a more descriptive table legend
Figure S1: improve quality of soil profile figure and state the authorship. Clarify the sampling depth shown in the figure and that expressed in methodology
Table S1: revise typo in the legend
Table S3: explain what is meant by indicator species analysis
Experimental design: Experimental design
Materials and Methods
Lines 93-95: if climatic conditions are provided, precipitation should be also included. This data is especially relevant given the climatic context of this work
Line 95: soil classification does not follow the nomenclature used by the USA Soil Taxonomy classification system, please revise and correct
Line 113: only one sampling depth is mentioned. It is not clear how this sampling strategy is related to the humus layer (see comment on the use of this terminology). This needs to be clarified, as it has implications on results such as that provided in Figure 4
Lines 123-124: explain this method better. How could you get water content from a dry sample?
Line 125: revise the use of the term humus layer. This terminology is not technically correct. Are you specifically referring to an O horizon or rather generalizing about a surface layer enriched in organic matter? I strongly suggest the correct use of edaphic terms
Lines 128-132: what was the area and soil depth for root sampling?
Line 156: what does PE stand for?
Validity of the findings: Validity of the findings
Results
Lines 193-195: text regarding indicator species analysis is not clear. This sentence is not informative
Lines 217-220: the text regarding network analysis does not add information to that already inferred from Venn diagrams
Discussion
Lines 238-340: this result is somehow expected, results should be more elaborated
Lines 247-250: same as comment above
Conclusions
Conclusion does not add novelty and it seems to be merely an abstract of the results presented through the text
Additional comments: The manuscript titled “Drivers and assemblies of soil eukaryotic microbes among different revegetation types in a semi-arid mountain in China” investigated the effect of different plant species used in soil restoration efforts at a site south of the Taihang Mountains in China, of semi-arid climate.
General comments
This work needs to be improved and a research hypothesis has to be included before publication. For further explanation, see specific comments below:
Abstract
Line 15: explain what would be meant by diversity and abundance
Line 19: why such comparison between protozoa and fungi? It is not clear the purpose of it
Introduction
Line 27: better specify to what is refer in the following sentence “Eukaryotic microorganisms are the dominant form of life” It this referred to biomass?
Line 30: revise the use of the word humus. In the context of the text it would be better to use the term organic matter. See article by Cotrufo et al 2015. Nature Geoscience for more insight into organic matter formation
Line 40: both articles sited took place in aquifer environments, this should be stated in the text to give an environmental context and contrast to the manuscript
Lines 40-42: in the text it is mentioned several studies have reported effects of organic fertilizers on eukaryotic communities. However, only one article has been cited.
Lines 44: what is sandtone 8?
Lack of hypothesis: this manuscript does not propose a hypothesis to test
Discussion
Lines 234-236: it is not clear what is the point of this sentence
Lines 237-238: this sentence is vague
Lines 258-262: it is not clear the connection of this statement with the discussion provided above in the same paragraph
Lines 269-272: what do the authors mean by “single OTUs”? are these singletons? If so, I would recommend removing these from the data set. Reasons on doing so are explained in the SOP by Schloss et al 2009
Lines 284-287: is this humus layer (see comment on terminology) present only in the forest soil? If so, this should be clearly explained starting from the methodology


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: DRIVERS AND ASSEMBLIES OF SOIL EUKARYOTIC MICROBES AMONG DIFFERENT SOIL HABITAT TYPES IN A SEMI-ARID MOUNTAIN IN CHINA
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment.
Experimental design: There are many errors in experimental design. For example, four dominant species Platycladus orientalis, Quercus variabilis, Robinia pseudoacacia and Lespedeza bicolor in forest, but the sampling design did not considered different species in the 12 independent plots, so the mixture sample can not represent the forest vegetation. On the other hand, changes in plant cover, increases in litter inputs, abundance of shrubs etc could explain diversity and composition of soil eukaryotic microbes, not only the SOM and fine root biomass.
Validity of the findings: No comment.
Additional comments: In this study the authors want to evaluate the species diversity and composition of soil eukaryotic microbes in artificial forest, artificial bush, farmland, and natural grassland at the south of the Taihang Mountain, China. My overall impression about this manuscript is negative. However, I also believe that there are plenty of aspects that can be improved for further study. Moreover, it needs careful round of editing, and careful going over the language by a professional, native speaker. There are too many awkwardnesses and grammatical errors.
Line 10-11. Rewrite for clarity. A variety of revegetation types include artificial forest and artificial bush, rather than farmland and natural grassland.
Line 36-45 and line 52-59. These description are not explicitly stated as a major goals for this study, this looks out of place.


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: DRIVERS AND ASSEMBLIES OF SOIL EUKARYOTIC MICROBES AMONG DIFFERENT SOIL HABITAT TYPES IN A SEMI-ARID MOUNTAIN IN CHINA
Review round: 2
Reviewer: 1

Output:
Basic reporting: The re- submitted manuscript titled “Drivers and assemblies of soil eukaryotic microbes among different re vegetation types in a semi-arid mountain in China” need further revision before publication.

Pay special attention to comments on methodology and results.

See comments on authors responses below
Experimental design: 5.This sentence includes supplementary information for the sampling area. If you think it is not connected with the rest of the paragraph, we will delete the sentence. We have deleted the part of introduction.（Line 110-111）
we established study plots, which were the main component of the ecological systems classified as the forest, shrub, grass, and farmland soil habitat types in October 2017
Do you mean?
we established study plots, which represented were the main component of the ecological systems classified as the forest, shrub, grass, and farmland soil habitat types in October 2017

6.The purpose of this picture was to introduce the sampling tool. We apologize for the poor picture quality, and we have deleted the picture. The soil sample and root samples were collected at a soil depth of 5–10 cm. We have revised the sampling methods.（Line 113-117）
Soil samples were collected at a soil depth of 5–10 cm and were taken along the “S” model from five sampling points, then pooled together as one large sample for each plot (understood). After cleaning up the impurities, 200 g term organic matter in the shallow soil was also collected (this is still not clear, what is the depth for this sample? how do you collect organic matter from a soil?). Root samples in the vicinity of the soil samples were also collected with a soil auger (inner diameter = 4cm) at a depth of 5–10 cm.

20. Soil water content = [(fresh soil quality) − (quality after drying)]/( fresh soil quality) × 100%

The water measurement method has been revised. （Line 126-128）
Thoroughly dried soil was used to calculate soil water content by comparing the quality difference between dry and fresh soil (This is called gravimetric water content and the way it is was calculated is incorrect. Please see a recognized soil science book, for example Nature and Properties of soil to get the correct calculation method)  . A soil auger were used to collect the term organic matter (five samples in a diagonal line for each plot), and the elemental analysis of term organic matter layer (is this referring to an organic horizon?) was measured by inductively coupled plasma mass spectrometry (Agilent Technologies, Palo Alto, CA, USA).
Validity of the findings: Findings need deeper argumentation
Additional comments: This manuscript is not yet ready for publication. There are some clarifications and corrections needed in methodology. Also, a deeper argumentation of network analyses would improve novelty of 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: ABERRANT REPAIR INITIATED BY THE ADENINE-DNA GLYCOSYLASE DOES NOT PLAY A ROLE IN UV-INDUCED MUTAGENESIS IN ESCHERICHIA COLI
Review round: 1
Reviewer: 1

Output:
Basic reporting: This a detailed work on enzymology, in the usual style of the laboratory. The interest of the research is clearly stated in the introduction and the experimental design is ok for me. The combination of biochemical experiments with complementary analyses in vivo using E. coly mutants make the results solid.
Experimental design: I think the design is appropriate.
I only have a minor question for the authors. It has been reported that some endonucleolytic repair activities are quite dependent on the sequence context. In particular I recall a work by the authors in which they show that uracil may be a substrate for APE1-mediated NIR, but this strongly depends on the sequence context. I wonder whether the authors have check MutY activity in different sequence contexts, in particular, mismatched DNA duplexes (AG/T=T or similar).
Validity of the findings: Data is enough robust.
Additional comments: My only main concern is the title of the work. I think that the title may be misleading. Negative results are still interesting, but the title suggests that MutY indeed has a role in UV-induced mutagenesis, while the clear conclusion of the paper is that MutY does not participate in that process. I suggest a title in line with the final conclusion.
I also would like that more clear information would be included in the figures. For instance, in figure 1, it would be helpful to denote somehow the difference between the two substrates with T=T and the sequence context. Similarly, the authors should indicate that in figure 2 some lines are controls with ssDNA or the genotype of strains in figure 4.


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: ABERRANT REPAIR INITIATED BY THE ADENINE-DNA GLYCOSYLASE DOES NOT PLAY A ROLE IN UV-INDUCED MUTAGENESIS IN ESCHERICHIA COLI
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is generally well written, using clear English throughout, although there are a few minor grammatical errors in places which need correcting.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: This manuscript describes aims to understand whether MutY plays a role in the repair of adenine residues opposite cyclobutane pyrimidine dimers (CPDs) and 6-4-photoproducts (6-4PP) generated by UV, and secondly whether MutY contributes to changes in mutation frequencies after UV irradiation. To my knowledge, this has not been investigated previously. The authors used a combination of in vitro biochemical assays using oligonucleotide substrates containing site specific CPD and 6-4PP damage in combination with MutY protein, and mutation frequency analysis in E.coli strains proficient or deficient in MutY following UV radiation. These experiments and results are all described and presented in sufficient detail.
The results from the study are largely against the hypothesis, but what these clearly demonstrate is that MutY is not capable of removing adenine opposite CPDs or 6-4PP in vitro from oligonucleotide substrates, but as expected is active in removal of adenine versus guanine or 8-oxoguanine (Figure 2 and 3). The authors also discovered that E.coli deficient in MutY do not harbour increased mutation frequencies in response to UV (Figure 5). However what they did find was an unexpected and interesting decrease in mutation frequency in MutY-deficient (BH980) and in MutY/NER (BH1220)-deficient strains. This decrease in mutation rates appeared to be dependent on the active protein, as demonstrated by complementation with wild type and not inactive MutY (Figure 5). The reason for this was not particular clear in the Discussion. Therefore my major comment would be to speculate on this finding given the observation that MutY clearly does not have an impact on repair of CPD or 6-4PP associated lesions at least in vitro.

Minor comments:
1. Some minor errors in grammar throughout the manuscript. For example, line 45 “regular bases resulted from“, should be “regular bases resulting from”; line 465 “evidences are accumulated”, should be “evidence has accumulated”. Line 486 should also state that “MutY does not recognise A opposite CPD or 6-4PP in duplex DNA”, to be more precise.
2. A correction to Figure 5 is required (is the MutY-D138N strain mislabelled as BH10701070 rather than BH1070?).
3. I suggest the incorporation of doses of UV radiation in Figures 4 and 5 for clarity, as these differ for the different strains.


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: ABERRANT REPAIR INITIATED BY THE ADENINE-DNA GLYCOSYLASE DOES NOT PLAY A ROLE IN UV-INDUCED MUTAGENESIS IN ESCHERICHIA COLI
Review round: 1
Reviewer: 3

Output:
Basic reporting: No comments
Experimental design: No comments
Validity of the findings: No comments
Additional comments: While DNA repair pathways are guardians of the genome, aberrant activity of these pathways may increase mutagenesis. In the past, Saparbaev and colleagues have already characterized one such aberrant activity of a base excision repair pathway. In this work, considering the increased UV-sensitivity of human XP cells producing a MutY homolog, they tested both in vivo and in vitro the possibility that E. coli MutY will act aberrantly on the UV-lesions, cyclobutane pyrimidine dimers and 6-4 photoproducts.

They assembled an oligonucleotide-based experimental system to detect MutY action on the strand opposite the pyrimidine dimers, using A-G mismatches as positive controls, but detected no cleavage, in two different sequence contexts.

At the same time, they show that in vivo, the mutY defect significantly (~10-fold) reduces increase in mutagenesis after UV, in both NER-proficient and -deficient backgrounds. The authors point out that this effect is due to the ~10-fold increase in the spontaneous mutagenesis in the mutY mutants.
	They explore this point further, by predicting and then demonstrating that before UV, ~85% of all base substitutions in the mutY mutants were the expected G—>T transversions, whereas after UV, ~70% of all base substitutions became C—>T transitions, indicative of TLS polymerase errors at pyrimidine dimers.

Finally, they consider published crystal structures and argue using measurements of inter-atomic distances that the structure of B-DNA around PD is significantly different from the structure of B-DNA around the A-oG mispair, apparently precluding recognition of the former by MutY enzyme.

Major points

(May be in the future, but…) I would also look at the opposite (PD-containing) strand for any MutY cleavage, just in case.

Minor points

It would be nice if the MS had page numbers. In the absence of these, I have assigned page 6 of the MS file (the title page) number 1, while all other pages are listed in relation to page 6. For example, Abstract is on page 3, while Introduction begins on page 5.

On page 13 (say, line 328), the authors should call mutY mutants this very name, or, at the least, should explain that micA is the mutY equivalent, — otherwise confusing. Also, the micA mutants are not BER-deficient, — they are deficient only in MutY!

On page 13 again, lines 340/341, I suggest to drop AB1157 results altogether, since the meaningful comparison here is between the uvrA and uvrA mutY mutants. This will allow to shorten the corresponding sentence and to combine the two current sentences on lines 340-345 into a single logical construct.

Page 18, lines 461-463 — this statement needs a citation (probably PMID: 26317348).

Fig. 6 — an explanatory panel showing the relevant structures would be helpful here.

Table 3 — in AB1157, the second category of base substitutions is T—>C, whereas for all other strains it is G—>T. Is this OK? It is not mentioned or rationalized anywhere…

Miscellaneous

Page 3, line 43 — insert comma after "exogenous factors"

Page 3, line 44 — insert comma after "do exist"

Page 3, line 45 — "resulting". Also, replace "and" with "or".

Page 3, line 50 — remove "which is". Also, replace "in" with "via"

Page 3, line 51 — Insert "However," before "MutY"

Page 3, line 60 — replace "cell survival" with "production of DNA repair enzymes"

Page 3, line 64 — replace "While" with "At the same time"

Page 5, line76 — insert two commas, one before "such as methylation", the other after

Page 5, line 80 — replace "in" with "via"

Page 5, line 82 — "presents"

Page 5, line 87 — replace "endogenous source of DNA damage" with "oxidative DNA lesion"

Page 5, line 89 — replace "damage" with "lesions"

Page 5, line 94 — replace "opposite to" with "across"

Page 5, line 98 — delete "were"

Page 6, line 104 — "Multiple evidence demonstrates"

Page 6, line 108 — Replace "Whereas" with "At the same time"

Page 6, line 110 — delete "dramatically"

Page 6, line 112 — replace "regular" with "correct". Also, delete "non-damaged". Also, replace "it's" with "it is".

Page 6, line 128 — delete "to"

Page 6, line 132 — replace "damage" with "lesions"

Page 7, line 140 — remove the comma and insert "the" instead

Page 7, line 145 — "evidence suggests"

Page 7, line 149 — replace "high-fidelity" with "replicative"

Page 7, line 154 — delete "to". Also, line 155. In general, delete "to" from combination "opposite to" throughout the text. I am stopping correcting this.

Page 7, line 156 — change "proposed" to "suspected"

Page 7, line 157 — replace "can" with "could"

Page 9, line 202 — replace "and" with "or"

Page 9, line 216 — replace "corresponding" with "the"

Page 10, line 232 — define PBS buffer

Page 11, line 261 — replace "for" with "in", in two places

Page 11, line 279 — insert "the" after "than"

Page 11, line 280 — "cleaves the remaining"

Page 11, line 282 — replace "Whereas" with "At the same time"

Page 12, line 292 — insert "the" after "reactions"

Page 12, line 298 — replace "and" with "or"

Page 13, line 339 — replace "Whereas" with "At the same time"

Page 13, line 340 — replace "Whereas" with "Similarly"

Page 14, line 348 — say: "strains exhibited 45-220-fold increase…"

Page 14, line 350 — replace "BER/NER and BER" with "mutY"

Page 14, line 363 — replace "Whereas" with "In contrast"

Page 14, line 366 — delete the comma

Page 17, line 422 — insert "the" in front of "absence"

Page 18, line 450 — insert comma before "and" and another one after "irradiation"

Page 18, line 453 — delete the first comma

Page 18, line 454 — replace "are" with "was"

Page 18, line 465 — "evidence accumulates"

Page 18, line 467 — delete "the"

Page 18, line 468 — "in the absence"

Page 19, line 478 — replace "were being protective" with "offered protection"

Page 19, line 479 — insert comma after "accumulation"

Page 25, line 717 — "doses"