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

Input:
Title: THE FIRST NORTH AMERICAN PROPTERODON (HYAENODONTA: HYAENODONTIDAE), A NEW SPECIES FROM THE LATE UINTAN OF UTAH
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall, this study represents an important contribution to the understanding of carnivore evolution in North American and Asia. Specifically, by identifying a new species of the otherwise Asian genus Propterodon it is evidence of an important exchange taking place between the continents. This new species is a significant data point for interpreting the diversity and ecology of carnivores during the Eocene in North America. This manuscript is also a testament to the importance of natural history collections as repositories and sources of new information on past and present ecosystems as the holotype was collected nearly eighty years ago.

This study is also exceedingly important because it reviews the history and taxonomy of Propterodon, a taxon that has been described in multiple languages over a century of work. This study will be a crucial resource for researchers investigating Eocene carnivores who need assistance hacking through the issues surrounding this important genus. This study supports the hypothesis that a species of Propterodon is sister-taxa of Hyaenodon - a speciose and wide-ranging hypercarnivorous genus. Propterodon is significant for interpreting the evolution of Hyaenodon, and this the first studies to directly address this important genus with a cladistic analysis.

The morphological descriptions are active, direct, and concise and the comparisons are thorough and appropriate, making a bulk of this paper acceptable as it is written. I only have a few concerns that I hope the author incorporates into a revision of the study to help make it more logically consistent and to ultimately make this an even more significant contribution. I also suggest a few figure modifications and additions that would illustrate the discussion featured in the manuscript. Finally, there are a few taxa mentioned in the discussion that are not included in the phylogenetic analysis. If possible, all hyaenodonts mentioned in the text in an evolutionary or biogeographic context should also be incorporated into the tree, or the author should explicitly describe why these taxa (Oxyaenodon in particular) were not incorporated into the phylogenetic analysis in the methods section.
Experimental design: The methods are appropriate to the question and the morphological descriptions are beautifully written. The comparisons are appropriate, barring a few suggestions in the General Comments section. I do think the methods used in TNT need to be made more specific so readers attempting to replicate the analysis can be confident they have followed the settings of the author when reproducing the study.

The major concern I have is that the methods section includes some discussion that undermines the larger conclusions of the manuscript. There is discussion in the methods about the superiority of this matrix over previously published matrices because it includes fewer correlated dental characters, but the criteria the author is using to determine what is a correlated character and what is an independent character is not explained.

Further, the author cites studies that argue dental morphology is unreliable as a source of phylogenetic information, then proceeds to name a new species based entirely on dental and proximal gnathic material, refer a species to a different genus based on dental morphology, and speculate on biogeographic exchange between two continents based on dental specimens. The discussion in the methods section caused me as the reader to wonder why the author trusted any of the succeeding comparative work if the author is so skeptical of the phylogenetic potential of dental morphology. The author's perspective on what qualifies as sufficient information to draw more than basic comparative conclusions should be expanded to make the following work logically consistent.

The discussion of OTUs should also be restructured to address the paraphyly of “Koholiinae” (a note expanded in General comments to the author). The methods section should also mention why relevant taxa evoked later in the manuscript are not included as OTUs, particularly Oxyaenodon.

Throughout the manuscript there are assertions about characters that are likely to be convergent and characters that are phylogenetically informative, but there is no method presented for how the author is making these determinations. It seems the author can either choose to make their assumptions more explicit, or the author can simply present the character-taxon matrix as they have chosen to construct it without making assertions about removing non-independent characters, a task that would seem difficult without a robust developmental perspective on genotypic correlation and its phenotypic expression.
Validity of the findings: The core of the study - the identification of an Asian genus in North American rocks – is important and valid. The larger context of exchange during the interval is also robust. One change I suggest is that the author spend less space identifying features that differentiate Oxyaenoides – a known and undisputed genus – from Propterodon – another uncontroversial genus and instead devote more space to contextualizing faunal exchange between North America and Asia during the late middle Eocene. The author focuses on the carnivore record, but a brief synopsis of other mammalian groups participating in this exchange would strengthen the utility of the manuscript for authors interested in larger-scale questions of ecological change.
Additional comments: Below are specific in-line comments for the author. They are a mix of practical and philosophical questions that will hopefully further strengthen the study:

Line 28: “…and appears unlikely.” This implies a likelihood or probabilistic method of phylogenetic inference was used. These methods were not employed in this study. In the methods section, while comparing the results of this study to many previous studies, the author should make it more clear that a different underlying model for phylogenetic inference is being used than has been employed by recent authors evaluating hyaenodont phylogeny. This language makes it sound like the author used Bayesian or likelihood methods, when they employed parsimony analysis.

Line 140: Borths and Stevens 2017 added deciduous dental characters to the character-taxon matrix. It is possible to test the phylogenetic position of Eoproviverra with a dp4 given published characters, or characters that can be modified. The selection of OTUs here is odd because it also doesn’t include all taxa relevant later in the discussion. Why is Oxyaenodon excluded from the analysis when it becomes relevant in the later discussion?

Line 147: The clade Koholiinae has not be recovered in recent analyses by Borths et al. Tinerhodon is resolved outside Hyaenodonta, Boualitomus and Lahimia are sister taxa, and Koholia is a very fragmentary specimen, though it is resolved along the stem of Hyainailouroidea. The blanket exclusion of discussion of this as a clade is not consistent with recent results. The absence of p1 is not known in Koholia because it is a fragmentary maxilla and the paracone of M1 may not be more distinctly lingual relative to the metacone than it is in Tritemnodon when wear is accounted for. The reasoning in this section should be reframed to note the possibility that Koholiinae is not monophyletic.

Line 167: Is there a reason the author refers to these as “minimum length trees” rather than “most parsimonious trees”? The latter is a more common term for referring to the resultant trees. Does this section imply there was a cap of 100 MPTs imposed in this analysis, or that the same number of MPTs were recovered by 100 separate analyses of the dataset? This description of the settings used in TNT should be more explicit. Based on this description, I am not confident I replicated the results via the same steps used by the author.

Line 222: The locality map is very simple and underutilizes space the color options available as a PeerJ publication. A basic geological map of Utah, or better a map of the basin with the Quarry situated in the larger sequence would be very useful. At present, the figure communicates little but political boundaries when it could communicate geological context.

Line 303: The author uses the phrase “closed trigonids” multiple times through the manuscript. At the first incidence of this morphology it would be useful to offer a brief explanation, describing how this is not synonymous with the presence of a large metaconid.

Line 323: Delete “below” or "before the end of"

Line 332: This is a confusing sentence that should be rephrased for clarity. Perhaps, “Unlike in Pyrocyon or Tritemnodon, m3 is distinctly larger than m2 in Furodon, Propterodon, and Oxyaenoides, a feature shared with P. witteri.”

Line 346: The structure of this sentence and the inclusion of the parentheticals makes it difficult to understand this section. I suggest the author restructure the sentence to make it easier to navigate the parentheses. For example, “Overall, Propterodon witteri displays a mixture of more derived morphology (open trigonids, trenchant talonids) and less derived morphologies (retained metaconids, elongate talonids) in comparison to Oxyaenoides.

Line 410: Note that Borths, Holroyd, and Seiffert 2016 and Borths and Seiffert 2017 used parsimony methods. The author’s comment holds in all of these cases with similar clades appearing, but low bootstrap support across much of the tree. It might support the point to mention these other parsimony results along with Rana et al. (2015).

Line 436: This discussion of the possible origins of Boritia is out of place in the results section as it speculates on relationships (Boritia + Prototomus) that are not resolved in the phylogenetic analysis. The results section should report what was resolved and move speculation on OTU origins to the discussion section.

Line 443: This section should be retitled “Hyaenodontine Sister-Taxa” or “Oxyaenoides and Hyaenodontinae” as it is essentially a description of the author’s skepticism that Oxyaenoides is a sister-taxon of Hyaenodontinae. This section amounts to an assertion that Oxyaenoides and Propterodon are distinct genera and Oxyaenoides is not the ancestor of Propterodon. I was not under the impression that any author explicitly argued that Oxyaenoides is the ancestor of Propterodon. No phylogenetic analysis can test for ancestor-descendant relationships. Humans are chimpanzees’ sister-taxon not their ancestor. Much of this section involves implicit and explicit discussion of ancestor-descendent relationships that cannot be evaluated given the patchy fossil record through this interval. This section can be used to express the author's skepticism that Oxyaenoides is the sister-taxon of Hyaenodontine, but the author should also note that in the phylogenetic analysis, the clade that includes Oxyaenoides and Matthodon is only one step removed from a sister-clade relationship to Hyaenodontinae.

Line 501: While the current organization makes sense, I wonder if it would be even easier for a reader to reference the new referral of Apataelurus pishigouensis if this was part of the Systematic Paleontology section. As formatted now, this important demonstration of the first Asian machaeroidine gets lost in the Discussion section. Another exceedingly useful addition would be a comparative figure illustrating Apataelurus pishigouensis and Apataelurus kayi. In addition to aiding the reader through the comparative section, such a figure would also help skimming readers recognize this paper includes the first Asian machaeroidine.

Line 502: Add a colon after Propterodon (“two additional Asian species of Propterodon:…”)

Line 565: “Among hyaenodonts, Oyaenodon dysodus does not appear to be derivable from Limnocyon potens” is a loaded statement with implied assumptions about the recovery of direct ancestor-descendent relationships. This early 20th century discussion contrasts with the author’s use of phylogenetic methods. It is possible to test whether the available morphological evidence supports a sister-taxon relationship between Oxyaenodon and Limnocyon, but the author does not use these species-level OTUs. As in the evaluation of the character differences between Oxyaenoides and Propterodon, the reader is left to discern the author's assumptions about morphological evolution. While important comparative commentary, such commentary does not yield reproducible results that can be built upon or tested by later researchers. One advantage of using cladisistic methods is researchers can be explicit in their models of evolution and can summarize comparative notes through a character-taxon matrix.

Figures: A figure like Figure 3 should be created to support the discussion of U1 and U2 faunas. The relevant taxa could also be incorporated into a more graphical presentation that uses a map, but a stratigraphic column that includes carnivoramorphans and other dispersing taxa would be very useful for the reader. Further, a figure, or at least an in-text, brief discussion of non carnivore exchanges during this interval would be exceedingly useful.


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

Input:
Title: THE FIRST NORTH AMERICAN PROPTERODON (HYAENODONTA: HYAENODONTIDAE), A NEW SPECIES FROM THE LATE UINTAN OF UTAH
Review round: 2
Reviewer: 1

Output:
Basic reporting: The revised manuscript addresses many of the questions I had about the initial submitted draft. The revised manuscript preserves the clear anatomical description and the comparative considerations raised by these specimens.

The restructured manuscript flows more easily and I believe it will be easier for readers to find the information they need within the text. The revised figure is effective and overall I think this will be a very useful document for carnivore researchers in the future.
Experimental design: The details of the TnT analysis were restructured in a way that allowed me to confidently replicate the phylogenetic tree. The explanations for OTUs included and excluded from the analysis were sufficient for me to follow the author's process.
Validity of the findings: The discussion and importance of the discovery, particularly the emphasis on the exchange between Asia and North American during this interval, and the evidence that museum collections remain a rich source of biodiversity discovery, make this an important and novel study. I am looking forward to engaging with the author's discussion and conclusions in my own work.
Additional comments: I greatly appreciate the author's time in addressing the questions I raised in my initial review of the study. This is a very exciting discovery and I look forward to seeing it in print in PeerJ.

Two very minor typos:

Line 100: Replace “character” with “characters”

Line 251/253: Insert space between “tooth” and “row”? This may be a style issue, but this seems like an unusual compound word.


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: ACCUMULATION OF DI-2-ETHYLHEXYL PHTHALATE FROM POLYVINYL CHLORIDE FLOORING INTO SETTLED HOUSE DUST AND THE EFFECT ON THE BACTERIAL COMMUNITY
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is well-written in good english and clear.
Literature references are recent and in context with the topic
the figures are well done.
Experimental design: The results are too preliminary because the control is not clear (there are not three duplicates) to have a comparative with the experimental data where the DEPH appears.
Validity of the findings: The results are too preliminary because the control is not clear (there are not three duplicates) to have a comparative with the experimental data where the DEPH appears. Is not clear if the effect is due to the DEPH or to any other factor. For example the population of other bacteria genera appears with DEPH, may be these bacteria are secreting some toxic compounds that inhibit the growth of the others, in fact some bacteria can secrete DEPH.
The authors may be should to have into account these possibilities and not to assign to DEPH the responsability of this inhibition.
Additional comments: One posible solution to known if the DEPH was the responsable of the decrement of the bacteria could be to put some DEPH concentration in vitro with different genera of bacteria that authors identificated in dust.
Otherwise is better to give some other posible explanations to explain the inhibition of some bacteria (antagonistic effect, or secreted secondary metabolites effect)


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: ACCUMULATION OF DI-2-ETHYLHEXYL PHTHALATE FROM POLYVINYL CHLORIDE FLOORING INTO SETTLED HOUSE DUST AND THE EFFECT ON THE BACTERIAL COMMUNITY
Review round: 1
Reviewer: 2

Output:
Basic reporting: The font in this paper should be uniform.
Page 9, line 133: 20C should be changed to 20 ℃
Experimental design: I would like more assurance as to quality of DEHP data in this study as the author did not give any information about the method blanks, recoveries and reproducible of matrix spiked samples.
Page 9, line 127-128： Not only the variance should be always below 10% for all injections, but also the linearity of calibration curves constructed for DEHP should be good (R2 > 0.99) over concentration ranges relevant to those in the samples.
Page 9, line 128: Have the author analyzed the levels of DEHP in procedure blanks to avoid the lab contamination? And have the authors used the internal standard to test the recoveries of the experimants?
Validity of the findings: Overall, this is an interesting paper that reports data relating to accumulation of di-2-ethylhexyl phthalate (DEHP) from polyvinyl chloride flooring to house dust and their effect on the bacterial community. The authors provide only three time points (1, 7, 14 days) to to test it, while more time points are needed for systematic study.
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: CHARCOT-MARIE-TOOTH TYPE 4B2 DEMYELINATING NEUROPATHY IN MINIATURE SCHNAUZER DOGS CAUSED BY A NOVEL SPLICING SBF2 (MTMR13) GENETIC VARIANT: A NEW SPONTANEOUS CLINICAL MODEL
Review round: 1
Reviewer: 1

Output:
Basic reporting: This is an interesting and well written study reporting a novel mutation in the SBF2 gene that cause a demyelinating neuropathy in miniature Schnauzer dogs.

In the introduction (lines 96-111) the authors review the canine genetic variants causing inherited polyneuropathies similar to CMT. It will be interesting for the readers if the authors enlarge the review and include also canine variants causing sensory and autonomic neuropathies. For example, the sensory-autonomic neuropathy in Border collies or the insensitivity to pain of hunting dogs ( Forman OP, Hitti RJ, Pettitt L, Jenkins CA, O'Brien DP, Shelton GD, De Risio L, Quintana RG, Beltran E, Mellersh C. An Inversion Disrupting FAM134B Is Associated with Sensory Neuropathy in the Border Collie Dog Breed. G3 (Bethesda). 2016 Sep 8;6(9):2687-92. doi: 10.1534/g3.116.027896. and Plassais J, Lagoutte L, Correard S, Paradis M, Guaguère E, Hédan B, Pommier A, Botherel N, Cadiergues MC, Pilorge P, Silversides D, Bizot M, Samuels M, Arnan C, Johnson R, Hitte C, Salbert G, Méreau A, Quignon P, Derrien T, André C. A Point Mutation in a lincRNA Upstream of GDNF Is Associated to a Canine Insensitivity to Pain: A Spontaneous Model for Human Sensory Neuropathies. PLoS Genet. 2016 Dec 29;12(12):e1006482. doi: 10.1371/journal.pgen.1006482.)
Experimental design: Experimental design is clear and the research is well within the aims and scope of the journal.
Validity of the findings: This represents the first report of a genetic variant in the SBF2 gene causing a naturally occurring polyneuropathy in miniature Schnauzers that is similar to CMT disease in humans. It represents a potential naturally occurring model for the human disease. I commend the authors for screening for the variant in such a large number of dogs of different breeds.
Additional comments: In the discussion the authors highlight all the advantages of using naturally occurring canine disease as a model for human diseases. It will be good to also include a paragraph mentioning the limitations of using canine diseases as models.


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: CHARCOT-MARIE-TOOTH TYPE 4B2 DEMYELINATING NEUROPATHY IN MINIATURE SCHNAUZER DOGS CAUSED BY A NOVEL SPLICING SBF2 (MTMR13) GENETIC VARIANT: A NEW SPONTANEOUS CLINICAL MODEL
Review round: 1
Reviewer: 2

Output:
Basic reporting: In this paper, Granger and colleagues describe the genetic mutation causing a demyelinating neuropathy in miniature Schnauzer dogs, previously described in another paper by the same authors. The paper is well-written, the genetic studies have been thoroughly performed despite the limited number of dogs. The discussion comparing the various phenotypes observed with different variants of the same gene is interesting and the literature review extensive. The figures are adequate and all necessary information has been provided. The paper is self-contained with a clear answer.
Experimental design: The paper fulfils the Aims and Scope of PeerJ. The research question is well-defined. The findings are novel and interesting. Investigation was rigorous using relevant techniques. No ethical issue has been identified.
All methods are thoroughly described.
Validity of the findings: As previously stated, all data have been provided and the results appear genuine and sounds. The conclusions are well stated.
Additional comments: -	Line 250: for the muscle biopsy, you may want to refer to reference 21.
-	Line 342: for consistency with line 344, name the mutations 2875C>T and 3586C>T.
-	Figure 1: please also add a scale bar to inserts C and D.
-	Figure 4B: please add the amino acid numbers to make it easier to the reader
-	Figure 4B: if codon GGT in control/GTA in affected dog corresponds to amino acid 773, can you please clarify why the premature codon is at amino acid 746?


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: STABILITY OF THE VAGINAL, ORAL, AND GUT MICROBIOTA ACROSS PREGNANCY AMONG AFRICAN AMERICAN WOMEN: THE EFFECT OF SOCIOECONOMIC STATUS AND ANTIBIOTIC EXPOSURE
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript reports on the stability of the vaginal, oral, and gut microbiota across pregnancy in African American women and examines the effect that socioeconomic status and antibiotic exposure has.

The use of the term ‘microbiome’ in the context of this manuscript is not appropriate.  ‘Microbiota’ should be used instead as this refers primarily to the analysis of 16S rRNA genes. See (Marchesi and Ravel., 2015. Microbiome 3:31) which provides an adequate definition of both terminologies.

Specific comments which relate to each section of this manuscript;

ABTRACT
-	Clear aims listed, with professional English used throughout manuscript.
-	In Line 43 you mention Shannon and Chao1 diversity and Bray-Curtis dissimilarity but do not specify that the former two are related to alpha diversity and the latter refers to beta-diversity. Please highlight this here instead of mentioning it in the results section.
-	The conclusion is simply a repeat of the results and does not include any closing statements.

INTRODUCTION
-	It would be helpful for the reader if you define what the microbiota is to provide clearer context.
-	The papers referenced on Line 63 (1 to 3) are not appropriate for the opening statement of this introduction. I suggest looking at microbial functions at different body sites e.g. gastrointestinal, vaginal and so forth for more appropriate references e.g. (Round and Mazmanian, 2009. Nat Rev Immuno, 9 (313-323). There is also a missing full stop after this sentence.
-	Again, look at the literature for more appropriate studies that have explored the role of the microbiota in infection, digestion, stress and so on (Line 64, 65 and 66).
-	On Line 70/71 you say [there have been...] “few studies that have investigated the role of the microbiome of other body sites during pregnancy.” but do not list them please provide them.
-	 Please provide references to the few studies you refer to on Line 72 to 75.
-	16S rRNA gene sequencing is not used to study the microbiome it is used to study the microbiota. Please make changes to this term (Line 77).
-	There is no mention of the defined community state types that are described in reference 26 (Ravel et al., 2011. Proc Natl Acad Sci U S A). Please describe them here. Results from MacIntyre et al., 2015. Sci Rep 5(8988) can also be discussed in this section.
-	In Line 86 you refer to L. iners as a species that produces less acid – are you making a point about pH here? If so, please elaborate or remove as it is a redundant comment.
-	In Line 89 you say little has been published in terms of evaluating the factors which contribute to differences in microbiome composition, but you have failed to mention studies that have looked specifically at racial/ethnic differences in general e.g. (Deschasaux et al., 2018. Nat Med. 24 (1526-1531)), (Brooks et al., 2018. PLoS Biol. 16(12): e2006842)) etc.
-	In Line 96 the paper (ref 31) correctly refers to the microbiota and not microbiome, please change.
-	Please highlight/re-iterate at the end of Line 98 why your study is important.
-	References needed for the sentence that finishes on Line 101.
-	sp. and spp. are not italicised (Line 119 and 122)
-	The sentence starting on Line 132 to 137 should be re-worded as it currently doesn’t make sense. You don’t use “16s rRNA gene sequencing of the microbiome”, you carry out 16S rRNA sequencing in samples (also written on Line 138).
-	Please include the most recent papers with regards to bacteria in the placenta and amniotic fluid or mention the fact these may be related to contamination (Line 143). There is a plethora of articles that have explored the presence of bacteria (or lack of) in the placenta over the last few years.
-	Please re-examine the literature with regards to your statement on Line 144/145 about there being few studies that have investigated the gut microbiota during pregnancy.
-	Provide references for the Sociodemographic features and prenatal microbiota section as none are given.
-	List the studies mentioned in Line 172/173.

METHODS
-	The metadata/raw data files have been opened with no problems encountered.
-       Figures and tables conform to guidelines.
-	The sentence starting on Line 314 should be revised as it does not currently read well.
-	The word “differences” is inappropriately italicised on line 324.

RESULTS
-	In line with typical results section formatting it would be more appropriate to introduce your participants at the start (Line 341 onwards) followed by a brief overview of the 16S rRNA sequencing data and then start a new paragraph which presents the sequencing results.
-	With regards to the 16S rRNA sequencing data section please clarify in more detail which samples were removed because it currently doesn’t read well.
-	The p values presented in Line 359 and 361 do not have a reference (i.e. which Tables they are derived from)
Experimental design: Specific comments which relate to each section of this manuscript;

INTRODUCTION
-	The goals of this study are clear and well defined (Line 181 to 193). Please consider using the common acronym, SES, for socioeconomic status.

METHODS
-	The participants were selected from the Emory University African American Vaginal, Oral, and Gut Microbiome in Pregnancy Study (ref 53) which is a robust and well-designed study.
-	The protocol review number is provided and has been viewed in the supplementary file. No issues found.
-	The DNA extraction methodology employed here is robust and is easily reproducible. The V3-V4 primers are fine but please be aware of primer limitations (this should be mentioned in the discussion).
-	Please clarify in the section related to DNA extraction, 16S rRNA gene library preparation and sequencing if a negative control/kit control was run as it is not mentioned. If this was not, provide justification as to why this did not occur (note that not running controls is not good practice). Several papers over the last few years provide means of dealing with kit contamination e.g. (Sheik et al., 2019. Front Microbiol. 9: 840).
-	The use of Qiime2 and dada2 is commended here.
-	Please clarify which software you used to perform the statistical analysis and include software version number.
-	Please provide reasoning behind comparing women who provided paired samples with those that didn’t (Line 285/286). This comparison is atypical and would normally involve a comparison between the women that provided paired samples and an independent comparison comparing those that did not contribute paired samples.
Validity of the findings: Specific comments which relate to each section of this manuscript;

DISCUSSION
-	In general, this discussion would benefit from being better contextualised with the relevant literature.
-	The opening statement of the discussion should provide a brief overview of the authors findings before drawing conclusions and findings from other relatable studies.
-	Ensure all studies are appropriately referenced through text.
-	The limitations of 16S rRNA sequencing should be better contextualised. It would also be noteworthy to mention primer design and contamination influences.
-	There appears to be no speculation on why these findings occurred. Please comment as appropriate.
Additional comments: STRENGTHS
-	This study addresses a literature gap of how the microbiota changes across body site after accounting for SES and antibiotic exposure.

WEAKNESSES
-	The literature review is not sufficient and does not provide enough or appropriate references. This manuscript would also benefit from being better contextualised in the discussion which is currently oversimplified with limited interpretation of the data.
-	Given the plethora of data generated from the 16S rRNA sequencing carried out it is surprising to see that taxonomy is not covered at all e.g. dominant genera found across body site. Moreover, there is the capacity to generate a number of very interesting graphs using the Phyloseq package that was employed for data analysis.

If this manuscript is to be recommended for PeerJ publication, all points made must be addressed.


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

Input:
Title: STABILITY OF THE VAGINAL, ORAL, AND GUT MICROBIOTA ACROSS PREGNANCY AMONG AFRICAN AMERICAN WOMEN: THE EFFECT OF SOCIOECONOMIC STATUS AND ANTIBIOTIC EXPOSURE
Review round: 1
Reviewer: 2

Output:
Basic reporting: This manuscript is quite well-written, well-referenced, well-structured and self-contained in the context of the state of the field.
Experimental design: The manuscript, which examines the correlations of the oral, vaginal and rectal microbiomes across pregnancy in women of varied socioeconomic status (etc.) seems to fit very well the Aims and Scope of this journal. The research questions ["to investigate: (1) the stability of the vaginal, oral, and gut microbioime from early (8-14 weeks) through later (24-30 weeks) pregnancy among African American women according to measures of socioeconomic status, accounting for prenatal antibiotic use; (2) whether measures of socioeconomic status are associated with changes in microbiome composition over pregnancy; and (3) whether exposure to prenatal antibiotics mediate any observed associations between measures of socioeconomic status and stability of the vaginal, oral, and gut microbiome across pregnancy] are well defined and have the potential to add to the overall state-of-the-field. There is no concern about the technical or ethical standards, and the methods are described sufficiently, with a single caveat. Line 260 states: "V3 and V4 regions of the 16S rRNA gene were amplified and tailed using target specific primers", citing a 2011 manuscript. It is not clear if these investigators used these primers, nor is their a discussion of the appropriateness of these primers for vaginal samples. Overall, this is a minor concern that should be readily addressed by the authors.
Validity of the findings: The data presented are appropriate. Filtering of the data was done according to rigorous and well-described standards. The results complement data from multiple other publications, but do not directly repeat any to any substantial degree. There is merit to the publication of these data. The data presented and the analysis of it are appropriate. The analysis is unique in there is almost no reference to specific taxa. The analysis and conclusion are based entirely on diversity (Shannon and Bray-Curtis) measures. Normally, there would be a reference to taxa present, absent, or changing in predominance across pregnancy. I would not suggest that the manuscript be refocused for this, but it is unusual. Overall, the data seem to be robust, and the statistical analysis sound.

The conclusions are well-expressed, not over-interpreted, and significant for the field. SES (and race) have been overlooked as variables in many publications and these variables seem to have a larger than expected effect. The conclusion that antibiotics seem to have no great impact is a very interesting and somewhat unexpected finding. The authors do not expand on this, but some thoughts about why this may be might be worthwhile adding to the manuscript.
Additional comments: This is a sound body of work and adds to the gestalt of our understanding of the correlations of the microbiome diversity (and composition) to the changes going on during pregnancy.


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: SEQUENCING AND ANALYSES ON CHLOROPLAST GENOMES OF TETRATAENIUM CANDICANS AND TWO ALLIES GIVE NEW INSIGHTS ON STRUCTURAL VARIANTS, DNA BARCODING AND PHYLOGENY IN APIACEAE SUBFAMILY APIOIDEAE
Review round: 1
Reviewer: 1

Output:
Basic reporting: English needs correction, errors and mistypings are present.
Experimental design: no coment
Validity of the findings: no comment
Additional comments: This study by Lu Kang and coauthors presents a very welcome and quite interesting plastid genomes of 4 representatives of the Apiaceae family. To my opinion, the authors obtained novel results of high interest for readers of PeerJ especially those working on molecular evolution of organelle genomes, plant barcoding and phylogeny.

Although I am very positive about this paper, it can not be accepted for publication in its current form and requires appropriate revisions. The main issue I see is the way the authors deal with plastome pseudogenes.

As follows from figure 2, Lu Kang et al have found ycf1 pseudogenization in Tetrataenium yunnanense plastome. This is very surprising as it is a very rare event, as far as I know ycf1 pseudogenization was reported only in some Passifloraceae, Fabaceae and Geraniaceae (putting aside monocots). Apiaceae ycf1 sequence alignment shows an insertion of 101 bases, 100 of which perfectly match with adjacent sequence, and this duplication looks like just an assembly error. However, I did not find in the manuscript any attempts to confirm the presence of pseudo-ycf1 in T. yunnanense by read mapping and PCR amplification and sequencing. If they were made, this fact should be reported in the manuscript, if they were not - they should be done.

Arracacia plastome hardly contains pseudo-rpoC1, because when annotation starts with the next Methionine downstream (see, for example, Prunus plastome KF990036), pseudo-rpoC1 will become uninterrupted and functional. This is just a matter of annotation, not pseudogenization.

Lu Kang and coauthors describe and discuss also other pseudogenes in Apiaceae plastomes. But everything retrieved from GeneBank should be checked twice, especially when the accession status is "unpublished". To my opinion, most of the discussed "pseudogenes" should be treated as putative unless confirmed by Sanger sequencing. The most abundant in putative pseudogenes plastome sequence of Carum carvi was obtained with pyrosequencing technology, the most drawback of which is problematic reading of mononucleotide stretches (see, for example, Tsuruta et al 2017, DOI:10.1371/journal.pone.0169992). When a stretch of 9A (instead of 10A) causes a frameshift, this is a doubtful frameshift and needs to be confirmed, but Peery (2015) did not report and, by the way, did not discuss anything concerning plastid pseudogenes! I wonder why, and I wonder why the authors believe that rpoB and rpoC2 (subunits of the plastid encoded RNA-polymerase, which transcribes photosynthesis-related genes) can be pseudogenized in non-parasitic/non-heterotrophic plant without checking it by themselves.

And the last, ycf68 and orf42 are extremely rare annotated (pseudo)genes. The authors also did not annotate them and did not describe them, giving the readers an opportunity to waste their time trying to find out what are the authors talking about. As for ycf15, currently two different ycf15 genes can be found in GeneBank plastome annotations: "real"-ycf15 directly after ycf2 and "fake"-ycf15 somewhere between rps12_3`end and trnV-GAC, what is more, in some accessions both are annotated as ycf15 (for example, Camellia japonica KU951523). The former is really pseudogenized, but Selineae members plastomes contain at least first 40 bases, and in Coriandrum full-length pseudo-ycf15 can be found, while the authors treat all of them "absent".

Summing up, this part of the manuscript should be rewritten or deleted, as it may require additional experimental work. Pseudogenes representing truncated copies of genes are just worth mentioning, as they arise due to the IR border shift, which is discussed properly in corresponding section.

Besides, I make a few comments as follows.
In Materials and Methods information about number of contigs and their length should be added, as well as stringency parameters used in GBlocks. As I mentioned above, reads mapping on the assembled genome sequences is necessary.

In Results the authors describe their own results and normally any references should be avoided, therefore text on lines 270-275 and 312-316 can be transferred to Discussion.
Line 449: " caused trnH(GUG)or psbA inversions" - not inversions, but duplications due to IR expansion at JLA.

Figures and Tables:
Figure 5 - unclear meaning of "P,R,C,F"
Table 2 - "unknown function" should be deleted, as ycf3 and ycf4 are photosystem assembly proteins. Just "open reading frames" is enough.


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: SEQUENCING AND ANALYSES ON CHLOROPLAST GENOMES OF TETRATAENIUM CANDICANS AND TWO ALLIES GIVE NEW INSIGHTS ON STRUCTURAL VARIANTS, DNA BARCODING AND PHYLOGENY IN APIACEAE SUBFAMILY APIOIDEAE
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript includes results of the research of four chloroplast genomes and phylogeny in Apiaceae subfamily Apioideae. By comparing the four chloroplast genomes with previous published data, universal 59 pseudogenization and shifting IR-LSC boundaries in Apiaceae were recognized. The manuscript has huge data, supported with figures and tables. The style of the presentation of the results in manuscript is simple and understandable, but a bit chaotic.
I have following remarks:
1.	In 283 type D shift is recalled for two Prangos species. Chloroplast genomes of three Prangos Lindl. species were published (MG386251, KY652265, KY652266) and D shift is recognized in all three species, that is why it will be correct to mention 3 Prangos species in the manuscript. Also, it will be interesting if two other Prangos cp genomes are included in phylogenic analyses of Apiaceae species.
2.	In 334 the novel insertion of 125bp is mentioned. It will be interesting to find if these sequences are matching to the sequences from other genomes (such as nuclear or mitochondrial).
3.	The manuscript has technical incorrections such as absence of gaps between the text and parentheses, absence of commas and others.
4.	Both Figure and Table legends should be expanded with details which help readers to understand their meaning.
Experimental design: no commen
Validity of the findings: no comment
Additional comments: In general, the manuscript is highly interesting from scientific point and results will be useful in further researches on species identiﬁcation, cp genome structure, population demography and phylogeny in Apiaceae subfamily Apioideae. I recommend this manuscript for publication after making corrections mostly of technical character.


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: SEQUENCING AND ANALYSES ON CHLOROPLAST GENOMES OF TETRATAENIUM CANDICANS AND TWO ALLIES GIVE NEW INSIGHTS ON STRUCTURAL VARIANTS, DNA BARCODING AND PHYLOGENY IN APIACEAE SUBFAMILY APIOIDEAE
Review round: 1
Reviewer: 3

Output:
Basic reporting: This manuscript was relatively well organized in the introduction, but authors messed the results and discussions up, which are main problems must be well reorganized before acceptance. The authors must strictly stick to only describe results they found basing on their own analyses. And leaving all comparisons between their findings and previous publications as well as description of results in previous publications to discussion if they were necessary. The secondly main problem is that shared CDS genes in plastomes of all Apiaceae species should be used for building phylogeny and performing following analyses instead of complete plastome, especially lots of pseudogenizations existed in the Apiaceae plastomes. Besides, add titles or necessary descriptions to the supplementary files.
Experimental design: Experiments in this manuscript were well designed, which used adequate techniques.
Validity of the findings: The main problems are that authors described too much findings basing on previous publications instead of their own data, which have been emphasised in above. Secondly, the "34 DNA segments and SSRs for phylogenic and phylogeographic studies" that were emphasised as part of main results were not clearly described and presented in the manuscript and supplementary files. Thirdly, "ubiquitous pesudogenization and two kinds of rare simultaneous contractions and expansion in five Tordyliinae species" were not really existed in comparing the number of pesudogenization  in the four newly sequenced plastomes with other species in the same family.
Additional comments: Authors must change the results and discussion in way like I have emphasised above before final acceptance decision.


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: SEQUENCING AND ANALYSES ON CHLOROPLAST GENOMES OF TETRATAENIUM CANDICANS AND TWO ALLIES GIVE NEW INSIGHTS ON STRUCTURAL VARIANTS, DNA BARCODING AND PHYLOGENY IN APIACEAE SUBFAMILY APIOIDEAE
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have made many improvements, and the current manuscript is of a much higher quality than the first version. The authors have adequately addressed my comments, but there are points, however, which make me feel that the manuscript is still not in a condition where it is ready for publication: figures and references. Correction of the text is still needed ("monophynic", "Selieae", "37 complete CDS sequences", "natural group", etc)
Experimental design: Experiments  well designed, appropriate methods used
Validity of the findings: no comment
Additional comments: I make several comments as follows.

1. The authors report results of newly performed phylogenetic analyses. Conclusions are the same, but I can not find the rationale for presenting a single ML tree without branch support values (Figure 6), while the authors declared ML analysis with bootstrap resampling. A "small" tree (Figure 7) is redundant, because it presents nothing new about non-monophyletic Tordylieae and nothing about tribes relationship, as the latter depends on root placement. So I suggest to add to the "big" tree bootstrap support values (higher than 50%) and remove Figure 7 with subsequent manuscript correction.
2. Figure 3: junctions indication is wrong and should be corrected. Some genes are shown also wrongly, because genes psbA, trnH, ycf1, ndhF, rps19 and adjacent rpl2 are transcribed in one direction, see my comments in annotated manuscript.
3. Legends to figures 1, 3 and 6 should be changed, I added suggestions in annotated manuscript.
4. Citations in the text do not correspond to the Reference list, I found 7 references not cited in the text and 3 citations not included in References.
5. "Phylogeny reconstruction" section of Materials & Methods contains a list of plants, which corresponds to their position in a phylogenetic tree, but looks like disordered. Why do not the authors arrange plants in alphabetical order (see, for example https://doi.org/10.7717/peerj.7830)? Genbank accession numbers for newly assembled plastomes also can be provided here.
6. Correction of the text is still needed ("monophynic", "Selieae", "37 complete CDS sequences", "natural group", etc)


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

Input:
Title: SEQUENCING AND ANALYSES ON CHLOROPLAST GENOMES OF TETRATAENIUM CANDICANS AND TWO ALLIES GIVE NEW INSIGHTS ON STRUCTURAL VARIANTS, DNA BARCODING AND PHYLOGENY IN APIACEAE SUBFAMILY APIOIDEAE
Review round: 2
Reviewer: 2

Output:
Basic reporting: The revised manuscript is basically ok now.
Experimental design: No more comments of experimental design.
Validity of the findings: But I still find that the annotations of gene rps12 and introns in the Figure 1 were wrong. Because the gene rps12 obviously cannot cover such large range in the plastome, which the present figure shows. Besides, introns are also not displayed in the Figure 1.
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: EXPERIMENTAL EVIDENCE OF CHEMICAL ATTRACTION IN THE MUTUALISTIC ZEBRA MUSSEL-KILLER SHRIMP SYSTEM
Review round: 1
Reviewer: 1

Output:
Basic reporting: BASIC REPORTING
Clear, unambiguous, professional English language used throughout
	The language is clear; still there are a few grammar mistakes to revise (e.g. Line 189-missing subject) and long sentences that could be improved; Lines 222-223 should be rephrased: the difference in activity was observed in the shrimps tested with different scents. It is noted a redundancy in the use of hypothetical verbs (e.g. Lines; ). “Killer shrimp” has the plural “killer shrimps”, which should be used when referring to experimental specimens or populations, while the singular “Killer Shrimp” can be used to design the species.
Intro & background to show context.
The context is well shown; however, the need of an experimental approach is not wwll justified. A change of the title is suggested, with the title being “Chemical attraction” and “experimental evidence” a subtitle.
In the Abstract, at line 25, the statement “shows for the first time” should be supported by a bibliographic analysis, including several species, a review that would be beyond the objectives of the experimental study. At lines 24-25, the absence of "learning"  was not shown by theexperiments - specific experiments could be designed for this, whereas, the chemical attraction observed appears a species-specific trait. At lines 27-28, “and perhaps other freshwater invasive species” is just a speculation, not supported by experimental data. Moreover, “perhaps” should be avoided in scientific papers. The keyword “synergy” is too general and could be applied in several other contexts.
Introduction - The definition of “plastic invader” (line 68) needs an explanation: invasive species may be physiologically or behaviourally plastic ( for behaviour, see: C. Rossano, G. Di Cristina, F. Scapini, 2013. Life cycle and behavioural traits of Dikerogammarus villosus (Sowinsky, 1894) (Amphipoda, Gammaridae) colonising an artificial fresh water basin in Tuscany (central Italy). CRUSTACEANA, 908-931).
Literature well referenced, relevant and updated.
Structure conforms to PeerJ standards and discipline norm.
Figures are relevant, high quality, well labelled & described.
Figure 1 should be integrated with a geographic map that locates Wales in a continental (European) context for international readers. This would also show the spread of the two invasive species, which is mentioned in the introduction and literature quoted. Figure 2 should be labelled to show where the shrimps were put into and then recorded, and the position of the substrates and chemicals they were subjected to. Figures 3-6 should report whether the killer shrimps were tested singly or in groups. In the figures where percentages are shown, the total number of tested individuals should be also reported.
Raw data supplied.
The day time when the experiments were conducted should be noted in the table. When percentages are shown, the total should also be given. For temperatures, the units should be added; in the excel table, please use the point for the decimals.
Experimental design: Original primary research within the Scope of the journal.
The paper reports a well conducted experimental study on chemical attraction of killer shrimps by zebra mussel.
Research question well defined, relevant & meaningful. It is stated how the research fills an identified knowledge gap.
However, the use of an experimental approach is not really justified, except by mentioning that it was done “for the first time”. The work hypotheses tested are just (with some shyness) put forward: “We hypothesized that killer shrimp might… further hypothesized that…might”. Moreover, there is a logical mistake in the use of “might” for a prediction. It is suggested to write a clear general hypothesis and list the two predictions.
Rigorous investigation performed to a high technical & ethical standard.
The experiments were well conducted and data correctly analysed. An ethics statement is included, important to avoid the dispersion of invasive species.
Methods described with detail & information to replicate.
It is suggested to add a table providing a synthetic description of the protocol used in the different experiments. Lines 113-117 of the Methods should be transferred to the Introduction, with the question and hypotheses to justify the approach, while the Methods should include the details of the experimental protocol. The heading of experiment 1 (Choice of zebra mussel density) is confusing because the subjects of the experiment were the killer shrimps, subjected to a choice. At line 147, the term “recognize” is not-properly used, because the choice was tested, not the "recognition", which would have implied an ad hoc experimental approach.
Validity of the findings: Impact and novelty are discussed with respect to management of biological invasions in freshwater bodies.
All underlying data have been provided; they are robust, statistically sound, & ontrolled.
The first statement in the Discussion at line 228 is speculative and was not shown by the results. It is suggested to stress the experimental evidence of the chemical attraction of the killer shrimp by the zebra mussel, while the reason (cause) for the joint occurrence of the two species may depend on several interacting factors. At lines 256 and successive, “group effect” is confounded with “social behaviour/sociability”, which was not shown by the experiments on killer shrimps: social behaviour would imply active interactions between individuals, while the group effect observed may have several different reasons (this could be discussed). Line 273: note that “chemical attraction” to other species is generally observed by predator species, including killer shrimps. The discussion at lines 274-287 extends to different amphipods, which should be listed, also mentioning their habitat (freshwater, bottom sea, rocky substrates, sandy substrates, intertidal, terrestrial, etc.), as amphipods are a large and diversified group. The result regarding the group facilitation reported at lines 288-289 should be better discussed, as it is relevant. At line 300-301, it is suggested that chemical attraction is an “older behavioural adaptation”, which, according to current evolutionary theory, is not contradictory to acquired behaviour – species-specific adaptation would be more appropriate to this context.
Conclusions are well stated, linked to original research question & limited to supporting results.
Additional comments: The manuscript is publishable, however it may be improved by:
1)	Adding a justification for the experimental approach within the issue of invasive species control;
2)	Avoiding subjective and hypothetical statements, which are not appropriate when reporting experimental evidence;
3)	Improving the figures and tables, including the supplementary material, by locating the populations tested in an European dimension, adding the total when percentages are given and providing the daytime of the experiments (important in behavioural studies. A table with an overview of the experimental protocol would be useful;
4)	Please, revise the English for grammar and syntax (e.g. use hypothetical verbs, long sentences)


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: EXPERIMENTAL EVIDENCE OF CHEMICAL ATTRACTION IN THE MUTUALISTIC ZEBRA MUSSEL-KILLER SHRIMP SYSTEM
Review round: 1
Reviewer: 2

Output:
Basic reporting: This paper was very well written.

A minor point is that scientific names are italicized in some references but not others.
Experimental design: The experimental design is fine, but the set up for the experiments is not adequate.  As the Introduction ends, I appreciate the study questions but the questions do not fully address the experiments that were conducted.  These should match better.  For example, why look at density when it comes to attraction?  What is the study question and why study it?  Why look at group dynamics?  Again, a good question but no set up for why it should be studied.
Validity of the findings: Findings are valid.  I would appreciate more discussion about why as the authors say on lines 314-315 "the presence of zebra mussel could make the killer shrimp more likely to become established."  This does not diminish the results, but I would like to see more speculation as to what they think is going on with this unique attraction.
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: REHABILITATION TIME HAS GREATER INFLUENCES ON SOIL MECHANICAL COMPOSITION AND ERODIBILITY THAN DOES REHABILITATION LAND TYPE IN THE HILLY-GULLY REGION OF THE LOESS PLATEAU, CHINA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The subject is exciting and will surely be of great importance for the management and recovery of degraded lands. However,  it should be returned to the authors for improvement and clarification so that it can be arbitrated correctly. I am very really looking forward to reading, the future improved version that I hope you will send us as soon as possible.
In the first place, the manuscript shows an abusive use of abbreviations, which makes it extremely difficult to read. Sometimes they forget to clarify the abbreviation, or it is written in two ways...
In the second term, and more importantly, the Introduction and Background needs to be deepened in order to understand the context of the processes. The article aims to be published in a magazine that has a global distribution and is not directed to botanists and soil scientists with specialisation in China, or to a reader to know about the area and its historical and environmental processes.
The literature used is only of Chinese authors, although this is fundamental for the bibliographical references of the studied processes, for the Introduction and necessarily in the Discussion, it should be able to be incorporated to authors also of world reference who are not only from the country.
Figure 1, the map of the area, does not allow to get an idea of the location of the area.
The tables must incorporate information to be explanatory and explain the meaning of the abbreviations. In turn, and linked to the list of plant species (exotic or native, tree, shrub, grass) I am not a botanist, and most readers will not be.
Experimental design: They should improve the clarity and explanation of the methodology in order to be able to read the results and discussion and understand their meaning. I suspended the reading and correction in Results.
I ask the authors: Did they describe the natural horizons of the soil (A, B, C) and their subhorizons? Is that they persist in an area as modified as it appears to be the study area. When they take samples in "five soil layers (0-10, 10-20, 20-30, 30-50, and 50-100 cm)", these correspond to what natural soil horizons? Which corresponds to each sample in each plot? Erosion must have been differential... Do they know? Alternatively, the modifications found in the Results may be influenced by them?
Is fundamental the authors be more explicit before being able to continue the review.
Unfortunately, in the version sent for review, the methods are not described in sufficient detail, nor are the information available is detailed to replicate the sampling.
Validity of the findings: To perform an analysis of the results and conclusions, the authors must make an effort to explain the methodology and why they have opted for it, and only in that case, I can proceed to perform the review and analyse the results correctly.
Additional comments: I suggest returning the manuscript to the authors to improve it and encourage the authors to improve it and to explain the methodology clearly.
I also ask you to incorporate the environmental history of that area, what is the type of soil, I see that it can be a fluvisol, but what kind of fluvisol is it? What natural horizons does it have? What is conserved in the original soil area? Alternatively, the soil disappeared, and they are analysing homogeneous sediment.
You also need to explain what was the original vegetation that gave rise to these soils. What kind of vegetation was used to revegetate (here are the scientific names, but they are too many for a reader to take the trouble to consult in each case what is. If it is exotic or native and if it is a tree, or bush or grass?). With what do the horizons sample in the manuscript correspond with the natural horizons of the soil?
Also, some photographs can complement the explanation.

I have annotated the PDF and upload it as part of my 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: REHABILITATION TIME HAS GREATER INFLUENCES ON SOIL MECHANICAL COMPOSITION AND ERODIBILITY THAN DOES REHABILITATION LAND TYPE IN THE HILLY-GULLY REGION OF THE LOESS PLATEAU, CHINA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The work seeks to find how to achieve a better soil rehabilitation in a region with strong erosion problems. The extent of the work and the amount of information collected make it very interesting and relevant, both for the journal and for the scientific community. This work highlights the relevance of time since rehabilitation begins and vegetation cover type. It has a very well documented background as well as a complete bibliography throughout the manuscript. I would like to thank the authors for sharing of raw data.
The article needs a revision for its writting. There are small mistakes or repeated statements in the same sentences. As an example, in lines 109-118 the statement “ensuring that all three plots within the site had the same rehabilitation time” was written four times in the paragraph.

2-The authors should unify the use of abbreviations such as MD and PD. For PD usage, I recommend the authors to use “PSD fractal dimension” instead, as "PD" is very similar to “PSD” it makes  reading less fluent.

3-From figure 2 to 7, each element contains 20 bar graphs in the same color and bringing little information  to the discussion. I recommend the authors to transform al this figures to tables or send it to supplementary materials. As they are shown in this manuscript,  are not useful for a better understanding of the article. Another option could be to make an x-y dispersion graph, plotting depth in y-axis for each vegetation type. This could aid to a better understanding of the results.
In case of maintaining bar graphs, Figures 5-7 could be reduced to one bar graph for each depth. It´s not necessary or recommended to graph the same value four times.
It is very difficult to understand the X-axis labels. The number appears to be in a strain

4-Line 89_Authors must also provide soil classification using an international soil description key such as FAO's one

5-In line 124-126 the authors should write down R software citation, as well as check this sentence as text "R version 3.4.4" is repeated.
Experimental design: About plot size selection, the authors used different plot size for each vegetation type. But they never explain why they did use different sizes, or how did they arrive to choose that size for each vegetation type. Also, there no mention about how they sample the Slopping cropland or the reference site.

Line 121-122 the authors are describing a composite sample and make no mention of the number of samples mixed.

It should have been mentioned that samples were brought to the lab before the 2mm mesh sieving, and not after.
Also, In line 122 they said samples were air dried, and then sent to the lab. In the lab,  sample were split in two, in which one part was refrigerated. I think the authors wanted to say the sample was split in two, in which one part was refrigerated and another air dried, before sieving.
Validity of the findings: No comment
Additional comments: I think it is an interesting work on a very important issue such as erosion in the hilly-gully region of the loess plateau. The reading of the introduction and discussion was very enjoyable, as well as being very well documented. Unfortunately, the graphics made it difficult for me to understand the article rather than facilitate it. I recommend improving the graphics to achieve a greater visual impact and not use so many abbreviations. Although they allow to provide more information, they can make reading difficult if they are many by making the reader look up the description above.


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

Input:
Title: REHABILITATION TIME HAS GREATER INFLUENCES ON SOIL MECHANICAL COMPOSITION AND ERODIBILITY THAN DOES REHABILITATION LAND TYPE IN THE HILLY-GULLY REGION OF THE LOESS PLATEAU, CHINA
Review round: 2
Reviewer: 1

Output:
Basic reporting: As expressed in my first evaluation, the topic is exciting, especially for its potential for the management and recovery of degraded lands. However, I consider that in the current state it cannot be accepted.
I must emphasize that in this second version the manuscript has substantially improved readability, by eliminating most of the unnecessary abbreviations by the authors and having homogenized the terminology, allowing a fluid and comprehensive reading.
However, although I understand that they have made an effort to attend to the suggestions made by the reviewers, the manuscript still does not have the argumentation to be published in an international journal such as PeerJ.
I believe that both the Introduction and the Background must have a deeper development so that the reader can better understand what the context and evolution of the degradation processes are.
I had argued in the previous evaluation that "The article aims to be published in a journal that has a global distribution and is not directed to botanists and soil scientists with specialisation in China, or to a reader to know about the area and its historical and environmental processes"
Figure 1 has improved substantially. But although they have incorporated other authors, they only appear added to the citations, but they do not contribute to the discussion or argumentation.
One topic in special is very important to me and I had suggested that it be taken into account, and I don't see it contemplated in the new version. In other words,  is not yet contemplated the clear analysis of the species of plants and the relationships with the restoration process (exotic or native, trees, shrubs, grasses), I am not botanist, and most readers will not be. But obviously the restoration should be related to the plant cover type. There is no analysis that takes into account the different adaptation of the vegetation because it is native or exotic, and because it is a shrub, tree or grass. Each has a different ecological function and a relationship with the soil, and that should be analyzed or discussed.
Experimental design: I consider that in the new version sent, the methods are described in a little more detail, as is the information available to replicate the sampling. About the multiple questions that I raised in my previous review, I do not find answers in the new version, I believe due to constraints of the methodology used by the authors, where they did not seek to answer them.
Validity of the findings: Now that I can read fluently without the abbreviations, analyzing the previous and current version, we feel that we do not find a great difference between the two, they lack a deep discussion of the results or a correlation with the ecological importance that these results would have.
Additional comments: I suggest returning the manuscript to the authors to make a substantial improvement. Although I understand that they have made corrections, I try to encourage the authors to read the article carefully and look for the idea they are trying to convey with it (given they are wanting to assign it to an international community of readers).
The current version, I see it suitable for a regional journal.
The environmental history of that area has not been incorporated, no questions were answered such as: What is conserved in the original area of the soil? I guess the soil disappeared and they are analyzing homogeneous sediments.
Nor is it clearly explained what was the original vegetation that gave rise to these soils. What type of vegetation was used to revegetate (here are the scientific names, but there are too many for a reader to bother to consult in each case what it is: if it is exotic or native and if it is a tree, shrub or grass?)
The built-in photographs do not adequately illustrate and lack legend, I suggest paying attention to the graphic presentation.


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 COMMAND-LINE BIOINFORMATICS TO BIOGUI
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript presents bioGUI for running bioinformatics software on Windows under the Windows Subsystem for Linux). Usability is a serious issue for software - particularly in the discipline of bioinformatics which includes a wide variety of software with even wider variability in long-term support. While the authors have identified an important need, it is difficult to understand how bioGUI would alleviate this problem. (1) The manuscript lacks a mature review of the current state of the field, listing only two workflows - one of which (Yabi) is sadly out of date. (2) The manuscript sets up CLI-aware vs. GUI-dependent end users as the two use cases; in reality, the distribution is much more nuanced as many "wet-lab" researchers are familiar enough with CLI to install software and run basic commands. No evidence is presented to support such a binary distinction. (3) There is no methodology described or referenced that explore the actual trouble spots in software usability except the authors stating that it is installation and use (which are vague enough to be generally useless). (4) There is no methodology for assessing whether bioGUI actually does make it easier to run bioinformatics software despite multiple statements that it does.
Experimental design: This manuscript describes a software package; as such, a traditional experimental design is not to be expected. However, from a usability standpoint the manuscript does not appear to design any experiments to determine appropriate trouble spots in bioinformatics software use. In addition, there are no experiments presented to assess the success of their software.
Validity of the findings: A stated in previous sections, there is no data presented here that can be evaluated. On first principles, it appears that bioGUI relies heavily on the implementation of Windows Subsystem for Linux that is developed by Microsoft. However, this is incidental to the value of  bioGUI, since any bioinformatics software can take advantage of the WSL. bioGUI appears to replace some CLI (software install and command run) with other command-like language (i.e., XML specifications) but it is not clear how (or if) this would improve usability. Finally, usability metrics would have been useful for gauging the actual value of bioGUI, but nothing is discussed in this regard.
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: FROM COMMAND-LINE BIOINFORMATICS TO BIOGUI
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors created a tool that allow users to generate graphical interfaces for existing bioinformatics tools, currently, only available through command line.
The article is well written and supply a good explanation regarding this tool importance. It is a relevant work and I am certain that it will help the community to gain access to bioinformatics, as much as, will help the developers to spread their tools.
In the current version, however, the tools seems limited to windows users, depending heavily on the integration through WSL (Linux subsystems). Moreover, after trying the tool, I got a few concerns regarding the range of its capabilities. I believe the paper could be more focused on which tools are currently supported and how they are integrated to the GUI and less on the importance of Graphical User Interface.
Below, I will point out the aspects that I believe need to be addressed in order for this work to be published.
Experimental design: No comments.
Validity of the findings: No comments.
Additional comments: In the introduction, the authors describe the problems of using tools like AlgoRun and among them they state that docker solutions to run this software depends on sophisticated configurations, rather than the simple WSL download. I disagree with such statement, as the simplicity to install bioinformatic tools on WSL will also depend on the characteristics of the WSL version and the installation of dependencies for the tool of interest. Such problems have been mentioned in the paper Morais et al., 2018 "BTW—Bioinformatics Through Windows: an easy-to-install package to analyze marker gene data." PeerJ 6 (2018): e5299, where some tools wouldn't work at all in the WSL, because of compilation issues. The authors of the aforementioned paper use the same strategy of bash scripts to install bioinformatic tools in WSL and there is already reports of complications depending on the tools being installed.

Although the authors mention the multi-platform nature of bioGUI (in the lines 62 and 121), there is way more emphasis on the windows platform in the abstract and in the online documentation for usability. Giving the impression that although it was designed in a cross-platform language, there is only support for Windows users. Is it possible to download it and run it from Mac and Ubuntu (or other Linux distribution)?

Regarding the XML templates for GUI, would be nice to have a figure or scheme with a simple example like trimmomatic and how a XML template should look like.
One suggestion to increase reproducibility, would be to have a log file of the bioinformatic commands used or some button (template example) for outputting this log file with the selected parameters for each bioinformatic tool.

After installing the tool in a Windows 10 machine, Build 15063, and running the program bioGUI, I found some templates, but was not able to use the available tools. Checking the user's guide, I found that it supplies initial instructions until the download of templates and installation of software, but it doesn't explain how to use the newly installed software. Also, when checking the folders under WSL to see if the new software was there, nothing was found. Apparently the installation had some issue that was not even reported.

The user's guide (https://biogui.readthedocs.io/en/latest/user_guide.html) also mentions a list of available templates but when we click on the link (https://www.bio.ifi.lmu.de/software/bioGUI), we are sent to an error page.

Moreover, when checking the list of available software, there is currently 15 tools available through bioGUI (none of which were actually running after my installation), this is almost the same number offered by SEED 2 by (Vetrovsky et al., 2018) SEED 2: a user-friendly platform for amplicon high-throughput sequencing data analyses. Bioinformatics. 2018 Feb 14;34(13):2292-4. The mentioned tool is focused on amplicon data analysis, which is a limited sub-field of bioinformatics. If bioGUI is meant to be a tool for the whole spectrum of tools in bioinformatics and if it is really as easy as a few minutes of work for someone to create a template (lines 64 and 65), I believe there should be way more templates and tools available to the community.

Small remarks:
I feel that for the broad audience and knowing that bioinformatic software is also made by domain-experts, would be interesting to include some brief explanations of the terms "Continuous Integration" and some examples of use, as a simple template creation example.

line 206 "reproducable" > "reproducible".


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 COMMAND-LINE BIOINFORMATICS TO BIOGUI
Review round: 1
Reviewer: 3

Output:
Basic reporting: No Comment.
Experimental design: No comment.
Validity of the findings: Joppich and Zimmer have identified the abundance of command line applications for bioinformatics as a common issue for life scientists who are not experts in the use of unix based computer systems. The authors of this manuscript aim to lower the barrier to entry for scientists by providing a program (bioGUI) to easily convert command line applications to a point-and-click format. While a user test case and a developer test case are described in the paper and appendix, data-driven assessment of bioGUI in the context of life scientist laboratory use and developer use are not described in the manuscript.

A theme within this manuscript is the use of laptops or laboratory computers for common bioinformatic analyses, such as high throughput sequencing analysis. The researchers use Galaxy and Yabi as examples of existing workflow systems for common laboratory analyses. Galaxy is often installed on compute nodes more powerful than the standard laboratory computer so as to handle the large size of the datasets generated by standard sequencing platforms and the compute power required to analyze these datasets appropriately. Have the researchers tested a “typical” laboratory computer for its use in the test cases described in the manuscript? The use case should include run time statistics including required storage, RAM and time required for the analysis to be completed. These requirements should be compared to a “typical” laboratory computer. Could access to a remote server or compute cluster be integrated into the templates by developers?

Additionally, while basecalling during MinIon data acquisition is one use special use case, describing the use of bioGUI with more common use cases (such as Illumina-based genome assembly, or RNA-seq analysis) would greatly strengthen the paper.
Additional comments: This manuscript contains combative language toward “wetlab” life scientists. It should be noted that life scientists are not incapable of using unix-systems and command-line based programs but rather their expertise is concentrated in other disciplines.  Please address the language in the manuscript for such bias.


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 COMMAND-LINE BIOINFORMATICS TO BIOGUI
Review round: 2
Reviewer: 1

Output:
Basic reporting: 1. Basic Reporting
This manuscript is improved from the original submission by the addition of a benchmarking study and numerous text changes. It represents a fairly comprehensive description of the authors' software, bioGUI. Some clarity has been added surrounding the different target audiences - developers and end-users - and this is helpful. A few concerns remain. (1) There is no methodology (described or referenced) that explores the actual trouble spots in bioinformatics software usability. This could be done with a fairly straightforward usability study or user survey. The lack of data to support the authors' fundamental assumptions detracts from the impact of the manuscript. The authors have added two citations (line 175), but these refer to personal communications that are not possible to evaluate. (2) The authors have added several benchmarking results that demonstrate well the function of their software on various hardware/OS combinations; however, there is no methodology for assessing whether bioGUI actually makes it easier to run bioinformatics software (e.g., pre- and post-testing). (3) The writing style is awkward, with dropped definite articles, misspelled words, and difficult phrasing throughout.

Specific comments:

Line 11 and beyond: An abbreviation for "command-line" (CL) is defined in line 10 and can be used throughout the rest of the manuscript.
Line 43: skeptical is misspelled.
Line 49: "when not yet running a software routinely on many data yet" - this phrasing is awkward and difficult to understand.
Line 63: GUI is already defined on line 41.
Line 95: "highly sensible" does not make sense in this context. is this supposed to be "highly sensitive" instead?
Line 109: CWL is already defined.
Lines 127-128: the use of italics here is not clear; if this is meant to be a direct quote, it should be surrounded by quotation marks.
Line 136: please replace "his" with "their."
Line 177: "command-line line" is redundant.
Lines 206-207: extra "the" between installed and software; also the last part about already being derived is confusing: "the path to the installed the software as well as other default values that can already be derived during the installation"
Lines 225-226: the reference to a petri net is not clear and should be removed, unless the authors propose that bioGUI can be treated mathematically as a bipartite directed graph to some advantage.
Line 246: execution is misspelled.
Line 338, 352-354: please clarify the interchangeable use of brew and homebrew. the package manager is called homebrew, while the executable for that manager is called brew.
Line 347: "from on" should be either "from" or "on" but not both.
Line 362: sub-processes should be singular.
Line 504: existent is misspelled.
Line 505: please change no to not.
Line 516: please change themselves to herself.
Line 527: analysis and hence are misspelled.
Line 544-546: the last two sentences of this paragraph are quite confusing and contain many hyphenated words that do not appear to require hyphenation.
Line 571: please replace "which's output" with "and then the output".
Experimental design: No comment
Validity of the findings: No comment
Additional comments: No additional comments


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

Input:
Title: FROM COMMAND-LINE BIOINFORMATICS TO BIOGUI
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comments.
Experimental design: No comments.
Validity of the findings: No comments.
Additional comments: I am glad to see that all my concerns were addressed and the paper was extended considerably. I am also happy to see that the general supporting material for the software was expanded. I am sure bioGUI is a very useful tool for the whole scientific community.


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 COMMAND-LINE BIOINFORMATICS TO BIOGUI
Review round: 3
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: The Methods section begins with several paragraphs describing systems already in existence. This information might be better placed in the Introduction as it does not describe methodology developed in this manuscript.
Validity of the findings: No comment.
Additional comments: No additional comments


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

Input:
Title: FIRST-TIER DETECTION OF INTRAGENOMIC 16S RRNA GENE VARIATION IN CULTURABLE ENDOPHYTIC BACTERIA FROM CACAO SEEDS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript was clearly written with clear language and sufficient background and references.  Figures are relevant and appropriately described. Although not strictly required, I recommend that the raw electropherograms produced for each culture should be made available in order to facilitate reanalysis and independent verification.
Experimental design: The research question was well-defined and the methods were described in sufficient detail to replicate the work. Unfortunately, the overall experimental design falls short of the necessary rigor to reach the authors’ conclusions.

It is clear that the authors have detected heterogeneity among the 16S rRNA gene sequences that can be amplified from their cultures. However, it was never shown that these cultures represent pure isolates. It is likely that they are instead enrichments of multiple organisms and that the heterogeneity observed can be attributed to intergenomic and not intragenomic heterogeneity. Three round of streak plating (lines 140-142) is not sufficient to establish a culture as being a pure isolate. Given that direct amplification of 16S rRNA genes is often used as a purity test, the obvious interpretation is that they do not have pure isolates. Therefore, the burden of proof lies on the authors to reasonably prove that their cultures are pure, more precisely, the authors must prove that their cultures were pure when they were used for generating the electropherograms and Alu1 resctriction patterns found in the manuscript. Unfortunately, it is quite difficult to recommend an alternative method of verifying purity of the cultures. Cloning 16S rRNA genes amplified from cultures would only verify heterogeneity and would not address the question of purity. Fluorescent in-situ hybridization (FISH) can be used to verify purity, but this procedure requires extensive experience and well-characterized primers, which if either too specific or two broad could easily lead to a misinterpretation. The only other alternative I can think of would be  either deep sequencing with short reads (e.g. Illumina) to rule out potential contaminants  or alternatively to sequence their cultures with long-read technology (e.g. Nanopore) to directly verify intragenomic rRNA gene heterogeneity.
Validity of the findings: Given the major problem identified with the experimental design (see section 2), the validity of the findings are seriously in question.
Additional comments: I appreciate the time and effort put into this manuscript and I appreciate how important this work is. The manuscript is clearly well organized and clearly written, which made it a pleasure to 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: FIRST-TIER DETECTION OF INTRAGENOMIC 16S RRNA GENE VARIATION IN CULTURABLE ENDOPHYTIC BACTERIA FROM CACAO SEEDS
Review round: 1
Reviewer: 2

Output:
Basic reporting: In their manuscript, authors B da Silva et al., propose a rapid, cost effective method for the detection of intragenomic 16S rRNA gene variation in culturable bacteria endoseeds from cacao plants. In general good English language is used throughout the manuscript (see minor specific comments). Introduction section in well presented and the literature is well referenced and relevant. Finally all figures are under PeerJ’s standards and the raw data are supplied.
Experimental design: Methods described with sufficient detail & information to replicate. More comments are included in the following section because they are a combination of used methods and obtained results.
Validity of the findings: The study deals with a well known problem for all diversity studies, no matter the ecosystem, the overestimation or not of the monitored diversity based on NGS results on the 16SrRNA gene. It is well documented that this problem is due to 1. multiple copy numbers of 16SrRNA gene within a cell, 2. horizontal gene transfer and 3. intragenomic 16S rRNA gene variation of the multiple copy numbers of 16SrRNA gene. Whole genome sequence at the single-cell level is a solution, for those bacteria that can be cultivated and for those who can afford the cost of this method. Combining culture dependant and dependant methods is a partial solution tho this problem, with the limitations described by the authors. In fact the authors have consider and reported all methodological limitations and drawbacks.
However, there is a lack in commenting on the hypervariable region of the 16SrRNA the authors targeted (V5-V9). There is a very interesting review of Sun et al. (2013), that is referenced by the authors, that highlights the region V4-V5 as with the less intragenomic variation. Could the authors please explain why they used V5-V9 region and discuss that according to their results. Do they believe that the region they target could lead to the patterns they monitor?
In addition, in my opinion, a more clear statement should be made on how this kind of analysis can help on assessing a more accurate diversity pattern of the ecosystem under study. The authors make an interesting remark on the introduction (L99-L101: “..to provide correction factors to compensate it”), however they don’t further discuss this in their manuscript.
Finally, as a comment, this kind of analysis could be a useful first finger-print for the expected diversity or identification of isolating the same bug multiple times, especially when you want to continue your analysis with searching for e.g. plant growth promoting traits for your isolates.
Additional comments: Minor comments:
1.L73 “ Bacterial strains with > 70% at the DNA reassociation level”: maybe to replace with DNA-DNA reassociation
2.L229-232: This sentence could be re-written in more simple way
3.L232 “ a single PCR amplicon”: do you mean single gel band? Could you please rephrase?
4.L244 “On the other hand”: This is not needed
5.L245: It is not clear for which electropherograms you performed in silico analysis
6.L345-350: Did you examined if there was any correlation in intragenomic variability at lower taxonomic level, eg family or genus of the full genomes used with the isolates tested?