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: ECOSYSTEM FUNCTIONAL RESPONSE ACROSS PRECIPITATION EXTREMES IN A SAGEBRUSH STEPPE
Review round: 1
Reviewer: 2

Output:
Basic reporting: •	Well-presented manuscript. I appreciated the additional details provided in the appendices, particularly appendix 2.
•	A more general ecology audience may benefit if the introduction would start with an additional first paragraph to provide a framing of the research in a larger picture and to explain why the ANPP--soil moisture relationship is so important.
Experimental design: •	I don’t understand the rationale for why the analysis is presented in terms of ANPP responses whereas NDVI was measured. The ANPP values represent a linear transformation of the NDVI measurements, but with a mediocre to low R2 (A1-2), e.g., R2 for year 2015 was 0.21 -- an information that is somewhat buried in the supplementary files. This less than ideal relationship is not discussed, e.g., as potential fourth source for not finding responses (lines 285-288). Why not analyzing NDVI--soil moisture relationships instead/in addition to ANPP--soil moisture relationships?
Validity of the findings: •	The interpretation/discussion is coherent with the results. Even though the study found no responses, I agree that this is a reasonable outcome for a shrub-dominated, semi-arid ecosystem.
•	The introduction presents the idea that there are four basic types of how ANPP responds to increases/decreases in soil moisture and that the time it takes to express a response will differ among different communities (lines 87-90). Even though the discussion section suggests that species life history traits (‘bet hedging’, lines 310-319) are important to understand the results of no treatment responses, I feel that it would be as important to discuss how the lifespan of species in the community in relation to the experimental duration of the treatments promotes/hinders the observation of responses.
o	Several of the dominant species (e.g., threetip sagebrush and bluebunch wheatgrass) have a lifespan that is much longer than the 5-year experiment; while other species in the community have shorter reproductive cycles. It seems that even with a 5-year experiment the longer-lived species of the experimental community may not have had sufficient time to (fully) respond and make it possible to observe measurable changes in the community composition/response.
o	I would find it interesting if the plant community analysis is additionally carried out separately for short-lived vs long-lived species (Fig. 4) -- based on the expectations that short-lived species have more ‘opportunities’ to respond/turnover than long-lived species.
Additional comments: •	Fig. 3: Misspelling in ‘increasing kernal bandwidth’ -- this should be ‘kernel’
•	Fig 4: Expand caption: explain that dots represents plots and dimensions represent species.


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: ECOSYSTEM FUNCTIONAL RESPONSE ACROSS PRECIPITATION EXTREMES IN A SAGEBRUSH STEPPE
Review round: 1
Reviewer: 3

Output:
Basic reporting: Clear and unambiguous, professional English used throughout.
The article must be written in English using clear and unambiguous text and must conform to professional standards of courtesy and expression.
Literature references, sufficient field background/context provided.
The article should include sufficient introduction and background to demonstrate how the work fits into the broader field of knowledge. Relevant prior literature should be appropriately referenced.

-	English is high quality with very few typos, though a few locations in text could use rephrasing to increase clarity. Some restructuring of the introduction is suggested to provide a more logical and engaging presentation of the topic. Whenever I had a question about a topic the authors were referring to, or a method they were using, their citations were sufficient for me to conduct further investigation. More discussion of prior work into the role of dominant species in determining ecosystem function may be warranted.

Professional article structure, figs, tables. Raw data shared.
The structure of the article should conform to an acceptable format of ‘standard sections’ (see our Instructions for Authors for our suggested format). Significant departures in structure should be made only if they significantly improve clarity or conform to a discipline-specific custom.

-	There are no significant departures from standard structure.

Figures should be relevant to the content of the article, of sufficient resolution, and appropriately described and labeled.

-	Overall figures are well designed and easy to read, but treatment colors don’t translate well into greyscale. More contrasting colors (in terms of light and dark) are suggested. Minor things about a couple of table and figure headings could be changed to improve clarity. See notes to authors.

All appropriate raw data has been made available in accordance with our Data Sharing policy.

-	Data is easy to find and download.

Self-contained with relevant results to hypotheses.
The submission should be ‘self-contained,’ should represent an appropriate ‘unit of publication’, and should include all results relevant to the hypothesis.
Coherent bodies of work should not be inappropriately subdivided merely to increase publication count.

-	Product is a self-contained research unit that doesn’t leave the reader wondering where the rest of the results are.
Experimental design: Original primary research within Aims and Scope of the journal.

-     Primary research in Environmental science.

Research question well defined, relevant & meaningful. It is stated how research fills an identified knowledge gap.

-     The research goal is to investigate how the sagebrush steppe ecosystem may respond to long-term climate extremes outside of historic norms. Since most predictive work is currently done using long-term correlations between ecosystem function and climate, but the climate is changing this is a pressing concern. The inherent variability of ecological responses across ecosystems means that each ecosystem needs assessment.

Rigorous investigation performed to a high technical & ethical standard.

-	Design of the experiment looks very much like it was completely specified ahead of time and largely adhered to throughout. Where adjustments to the initial design were made, (probably in the soil moisture modeling) the procedure by which this was done was completely laid out. Though this is one of the areas I thought could use some rephrasing to increase clarity. The modeling work is excellent and looks at many different aspects of the question.

Methods described with sufficient detail & information to replicate.

- Generally, the methods are quite detailed, including the description of the statistical analysis so reproduction should be possible. There were a few sections I thought could use additional clarification and these have been addressed in the comments to the authors.
Validity of the findings: Impact and novelty not assessed. Negative/inconclusive results accepted. Meaningful replication encouraged where rationale & benefit to literature is clearly stated.

-	Many of the findings of this paper were negative, i.e. no change in ecosystem function or composition was observed. The authors draw the appropriate conservative conclusions of no effect. They do however discuss the possible implications of the positive and negative lean in the data, which might make for interesting grounds for future research.

Data is robust, statistically sound, & controlled.

-	Sample size is not large, though neither is it tiny. It was analyzed in such a way that information could still be learned despite the smaller sample size. Appropriate controls were included, though I would like a bit more information on why they used the controls they did, see comments to authors.

Conclusion are well stated, linked to original research question & limited to supporting results.

-	Conclusions are clear and do not reach beyond the scope of the data.

Speculation is welcome, but should be identified as such.

-	Authors speculated at length regarding why negative results were found. Concluding that it was likely a property of the ecosystem and probably not an artifact of the way the experiment was carried out, though they were careful to state that this possibility could not be ruled out.
Additional comments: This is a good article that yields insight into how experimental work can allow us to test whether historic precipitation/biomass relationships will told up to potential future changes in the precipitation regime. Overall, this is a very strong study and paper; it will make an excellent contribution to the scientific literature. However, there are some small issues that should be resolved first. There are some organizational issues in the Introduction; particularly, it seems the motivation for the study is buried deep within the text instead of in the first paragraph. Revising this section would make the paper a much more compelling read. Additionally, there were a number of places in the methods where I felt that additional clarity was needed so that others could replicate their study. Below I give line-by-line suggestions on these points and other minor editing suggestions. This reviewer feels that this paper should be accepted with minor revisions.

General comments to authors

Lines 31-32: sentence beginning with “However, ANPP response…” seems fairly vague and weakly worded, consider revising to increase clarity

Introduction:
While the abstract opens with a strong justification tying the paper into shifting precipitation patterns as a result of climate change and the need to develop a way to predict how communities might change with long-term exposure, the introduction opens only with a statement saying that there is a relationship between soil moisture and ANPP. This seems incredibly weak and uncompelling. The authors should consider restructuring their introduction so that the justification for their study is at the beginning. They have several other paragraphs in the paper that could do nicely as an opening paragraph. The opening paragraph of the discussion Lines 262-269 would make for an excellent opening. Or, with a little retooling the second paragraph of the introduction (lines 53-64) would make for a better statement of research motivation than the current opening.
Line 46 “outside” is repeated twice
Lines 71-72. While this is an excellent and clear definition of ‘ecosystem functional response’, I think it might be prudent at some point to explain why the authors are using soil moisture as an explanatory variable for ANPP instead of soil moisture. I agree that soil moisture is generally a better predictor of ANPP than direct precipitation measures, but most of the articles the authors cite refer to
ANPP-precipitation relationships, so taking a moment to explain why they are using soil moisture would be warranted.
Lines 88-90: another good motivating factor for why this research was done that could be used earlier in the introduction.
Final paragraph on introduction. I really like the way the authors are testing multiple hypothesis based on theory.

Methods:
110-113: Could the authors please explain why these long-term monitoring plots make better controls than just say a generic 1 m2 plot within the exclosures next to the experimental plots. Certainly the long-term record on community shifts in these plots are likely interesting in their own right, but it doesn’t seem like they add much to the current study.
Lines 126-127: It does concern me that the authors didn’t account for snow/winter precipitation on their irrigation plots. It appears as though a large percentage of the yearly precipitation in Dubois, ID falls over winter. Additionally, since their drought shelters were left up over winter they may actually have attracted drifting and captured more snow on the plots. To their credit, the authors did address this issue to some extent in the Discussion, lines 305-306.
Lines 132-135: Wasn’t initially clear that these were manually collected data instead of another set of sensors. Maybe mention that they were collected by handheld probe at the beginning of the description instead of at the very end.
Lines 142-147: Description of standardization procedure is confusing. I had to read it three times before the procedure was clear to me. Consider rewording for clarity.
Lines 148-158: I’m a bit confused on which plots this modeling was conducted for. Was it done only on those plots that had permanent sensors in place? Or when possible was it also extrapolated to include those plots that only had point in time measurements. Please clarify.
Lines 168-174: I like the idea of using the two separate estimates of greenness and then using the one that predicts best every year. Very thorough.
Line 188: later, in figure 2, the authors refer to mean volumetric water content as “VWC” also. It would be best to use a different abbreviation for the two separate uses of volumetric water content: mean and cumulative.

Results:
Lines 241-244: Even though figures are referred to here, it might be nice to have some measure of the effect size in text, perhaps percentages, just to give a numerical estimation of differences, or lack there of, between plots in ANPP and soil moisture.
Lines 257-260: the stability of the community over the study was impressive particularly given a method sensitive to rare species was used. It would be nice to see a bit more description of what the community looked like. How much of the community was the dominants, vs. rarer species?

Discussion:
Lines 279-281: I like that the authors were very conservative in their eventual conclusions despite their discussion of the potential meanings of the parameter estimates when these simply leaned positively or negatively and all overlapped zero.
Lines 289-299: strong discussion and support for the sizes of the treatment applied. Good work.
Lines 320-325: seems like authors are indicating that ecosystem response was driven by the response of the dominant species. Might be good to bring in some other work that has found similar results and discuss it a bit, for example: “Drivers of Variation in Aboveground Net Primary Productivity and Plant Community Composition Differ Across a Broad Precipitation Gradient” (La Pierre et al., 2016).

Figures and tables:
Table 1: These are the beta coefficents from the model correct? Might be good to elaborate a bit more in the table description.
Figure 2: Here is the use of VWC as “mean soil volumetric water content” I referred to earlier. Like I said it would probably be best to have different abbreviations for different metrics of soil moisture. Also interesting, though not the point of this paper, after three consecutive dry years with progressively decreasing ANPP it looks like the ecosystem was primed for recovery as soon as an average precipitation year hit in 2015. No evidence of drought legacy.
Figures general: differences between colors used to indicate treatments are not at all distinguishable if viewed in greyscale. Authors should consider using a color scheme with more contrast.


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: ECOSYSTEM FUNCTIONAL RESPONSE ACROSS PRECIPITATION EXTREMES IN A SAGEBRUSH STEPPE
Review round: 2
Reviewer: 1

Output:
Basic reporting: As before, the reporting and writing are very clear
Experimental design: As before, the experimental design is good. I doubt it changed during revision.
Validity of the findings: The authors have done an excellent job of addressing my concerns. The sensitivity analysis adds a new aspect to the study, and the authors did a great job discussing why their results do not conform to the expected patterns from other studies.
Additional comments: Thanks for the hard work! Nice job on the revisions. -Nate


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: ECOSYSTEM FUNCTIONAL RESPONSE ACROSS PRECIPITATION EXTREMES IN A SAGEBRUSH STEPPE
Review round: 2
Reviewer: 2

Output:
Basic reporting: A thoughtfully revised and improved manuscript; addressed all comments of reviewers with care and detail
Experimental design: Complete
Validity of the findings: Complete
Additional comments: - line 125: "n = 8 irrigation plots, and n = 8 irrigation plots" í one of two sets of n = 8 should be drought plots?


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

Input:
Title: ESTABLISHMENT AND QUALITY EVALUATION OF A GLIOMA BIOBANK IN BEIJING TIANTAN HOSPITAL
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article's English language quality is fairly good but it can be improved.

Some points need to checked/clarified:
- lines 81, 116, 128: use of 100g or 100mg or tissue?
- lines 49, 182, meaning of "period of storage" unclear: Samples were collected during the period 2011-2015. The storage period refers to the time between collection and analysis - eg if the analysis was conducted in 2016, the storage period may have varied between 1 and 6 years and not "at least 5 years" as mentioned in the text.
- lines 80-82: If the frozen tissue was placed into the tube containing TRIZOL (liquid), pulverization would generate a homogenate, not a powder, and it would be more appropriate to speak of "homogenisation" rather than "pulverization".
- line 129: what does the RIPA reagent do? i.e. why was this incubation done? e.g. to solubilize proteins?
Experimental design: The basic aim of the study, ie to evaluate the quality and suitability for specific types of analysis of tissues kept in cold storage for a number of years is well defined and the study design is generally appropriate. Rightly attention is focused on the quality of RNA, a particularly unstable material, and its appropriateness for different types of analysis. Regarding the latter, only suitability for RT-PCR was tested, focusing on just 2 genes. An analogous but more serious problem exists regarding the quality assessment of the protein content of the samples, where only a single protein was evaluated.
Validity of the findings: The evaluation of RNA quality by RT-PCR for just 2 genes is far from sufficient to allow any generalisation regarding the state of RNA molecules in general and some global gene expression analyses (microarray or sequencing-based) would be necessary for such an evaluation. While the RIN numbers suggest that most of the samples would be OK for transcriptomics, the limitation represented by the absence of global analyses should be noted and discussed. Similarly, the size analysis of just one protein says very little regarding the state of the samples, making statements like "Protein degradation was not found from western blot analysis" inappropriate.

The study's conclusions need to be modifed to acknowledge the above important limitations.
Additional comments: No additional comments


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

Input:
Title: ESTABLISHMENT AND QUALITY EVALUATION OF A GLIOMA BIOBANK IN BEIJING TIANTAN HOSPITAL
Review round: 1
Reviewer: 2

Output:
Basic reporting: This article describes the efforts of a glioma biobank to test the quality of samples that have been stored in liquid nitrogen for up to 5 years. The authors provided sufficient background and, for the most part, included sufficient references (exceptions are noted below), within their manuscript. The structure of the article conforms to the standard format and is a self-contained work.

Overall, the English language should be improved. In many cases the wrong word is used, there are grammatical mistakes, or articles are missing or misused. For example line 29, the word “remain,” line 45 the word “advantage”, line 72 the words “following evaluation,” or line 208 the word “pattern” were the wrong word choice and make the text difficult to understand. It was also unclear what the author’s meant by a “standard” glioma biobank (lines 22 and 46). The author’s would benefit from having a native English speaker edit their work.

Raw data has been made available; however, the consent document was in Chinese, so I was unable to evaluate its content. Details about figures and raw data are discussed in following sections.
Experimental design: This publication includes primary research that is within the Aims and Scope of the journal. The research question (whether the samples stored within the biobank maintain their quality over time) was well-defined. This manuscript provides some evidence to support the author’s assertion that their samples are of good quality and maintain that quality over time. However, issues with their assay choices (as described below) limit its usefulness to other biobanks who may want to apply their techniques or to researchers requesting their samples who want to be assured of their quality.

The methods, for the most part, were well described. Clarification on the following would improve the ability for researchers to understand the methods and replicate the findings:
•	Line 62, it’s unclear what the authors mean by “the rest of the tissue samples were gathered.”
•	Line 73, clarify whether the tissue samples were thawed before being placed in formalin or not.
•	Line 109, clarify if the “measurement” that was performed in triplicate was the entire qPCR experiment or the same sample was run three different times in the same experiment.
•	Line 134-136, the authors should specify how much protein was run from each sample on the gel (assuming it was the same amount for each sample) and should provide specifics about the product number and details (polyclonal or monoclonal) of the anti-ACTB antibody.
Validity of the findings: Composition of the Biobank:
•	Clarification in line 145 if 3,686 patients were consented and tissue was collected from each patient or if 3,686 tissue aliquots have been collected from a smaller number
of consented patients.

Morphological Characteristics:
•	Figure 2, the authors should indicate whether or not these are representative images from the 100 samples they looked at or they only looked at 25 H&E slides.
•	In line 150, how was “cellular decomposition” evaluated or quantitated (if it was quantitated)?

RNA analysis:
•	The authors should have shown or mentioned the A260/280 data to provide additional support (or as a comparison to the RIN and qPCR data) for their RNA quality results.
•	Table 1 and Figure 3 are redundant.
•	In Table 2, it is unclear why samples without a RIN score would have acceptable Ct values. This should be explained in Table 2 and in the text.
•	In Figure 3, the authors should indicate why several RIN scores were N/A. In these cases, could the samples have been run again to get a RIN score?

DNA quality analysis:
•	When evaluating DNA quality, the authors should have provided the 260/280 results as an indicator of DNA purity in their genomic DNA preps.
•	Genomic DNA quality can only be measured by qPCR analysis if the primers used result in long reads, which would show that the DNA has not degraded.  For example, in LePage et al (Biopreservation and Biobanking April 2013: 83-93) http://online.liebertpub.com/doi/pdfplus/10.1089/bio.2012.0044, the authors use qPCR to evaluate DNA quality looking at 4 different length fragments of the beta-globin gene. Could the authors please clarify how their qPCR evaluates DNA quality?
•	Figure 5 and Table 3 are redundant.
•	On lines 119-126, the authors should change RT-qPCR to just qPCR (because there is no reverse transcription step when analyzing genomic DNA) and change cDNA to genomic DNA.

Western Blot:
•	It is unclear how one Western blot looking at one gene is able to assess protein quality or degradation. Could the author’s provide additional details?
•	Most of the original files for the western blots appear to have increased contrast, making it difficult to evaluate if there are other bands or protein degradation on the blot.

Discussion:
The authors conclude that RNA, DNA, and proteins maintain their high quality even after being stored for up to 5 years.  However, based on the analyses presented throughout the paper, I am unconvinced that their data provides the evidence tosupport this conclusion. In particular, the protein and DNA quality assays, I do not believe show that the proteins or DNA are not degraded or not. Perhaps the authors could provide more justification as to why they drew these conclusions. The authors also mention that the Ct values were “stable” (lines 190 and 200), which they conclude means that there wasn’t RNA or DNA degradation. It’s unclear what is meant by “stable” and how this relate to RNA or DNA quality.
Additional comments: No additional comments


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

Input:
Title: ESTABLISHMENT AND QUALITY EVALUATION OF A GLIOMA BIOBANK IN BEIJING TIANTAN HOSPITAL
Review round: 2
Reviewer: 1

Output:
Basic reporting: The English language in the article continues to need some work. As stated in the original review, there continue to be issues with grammar, articles, spelling, and misused words. Examples of this include (but are not limited to): “staffs” on lines 23 and 62, “the word choice of “remain” on line 29, the use of the work “normative on line 48,the verb “were” (should be “was”) on line 71, word choice “removed” on line 86, misspelling on “moleculers” on line 215, etc. The author’s would benefit from review by an English-speaking editor.

Raw data was provided, however I was unable to open the .rar file containing the Beta-globin results and therefore could not evaluate that data.
Experimental design: The majority of the concerns with experimental design were addressed in the updated manuscript except for adding information about the antibodies used for the Western Blot.

The author’s added Beta-globin analysis to look at DNA quality, but did not provide rationale for this type of experiment or the reference citing the LePage article. Both would be needed additions.
Validity of the findings: The author’s addressed the majority of the concerns from the initial review.   The addition of the A260/A280 data figure was appropriate and this reviewer appreciated the author's re-running the samples with N/A for RIN scores from the original manuscript. The addition of the Beta-globin analysis for DNA quality should be shown as a figure or be provided in an accessible format for evaluation and as supplemental information.

The Western Blot and protein quality data does not assess protein quality. Although the authors add text in the discussion saying that this experiment doesn’t mean that all proteins are of good quality, this reviewer would suggest that the protein analysis data be removed from the manuscript altogether.  It does not add anything of value to the article.
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: STRONG GENETIC DIFFERENTIATION IN TROPICAL SEAGRASS ENHALUS ACOROIDES (HYDROCHARITACEAE) AT THE INDO-MALAY ARCHIPELAGO REVEALED BY MICROSATELLITE DNA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is riddles with inconsistencies in both grammar and spelling. Once the appropriate revisions have been made, the MS will need to go to a native English speaker for rewriting and checking. More detail is given in the 'general comments to authors section'.
Experimental design: ok
Validity of the findings: some misgivings in places - see general comments.
Additional comments: Review of “Strong genetic differentiation in tropical seagrass Enhalus acoroides (Hydrocharitaceae) at the Indo-Malay Archipelago revealed by microsatellite DNA” by Putra et al.
This paper examines the genetic diversity and phylogeography of the seagrass,  Enhalus acoroides, in the Indo-Malay Archipelago. The major conclusions of this paper are that this seagrass exhibits a high level of genetic diversity and structure. Three genetic clusters of populations were identified, with significant differentiation between populations on either side of the Sunda shelf. Several explanations are given for the pattern of genetic structure observed. Overall, I feel that this paper makes a meaningful contribution to uncovering phylogeographic patterns and barriers in the region, especially as phylogeographic studies on these important foundational species are absent from this region. I have no major comments on the science, but there are many grammatical errors which detract from the overall impression of the paper. I suggest that this paper is publishable, as long as the authors conduct an extensive grammatical revision and address the comments below. The paper will need to be seen again by the reviewers before it can be accepted.
Major comments-
•	An extensive grammatical revision will be required, specifically in the introduction and discussion, but also elsewhere. I have pointed out some of these as an example, but have not continued with grammatical editing past line 105.

•	There is a lot of discussion around genetic diversity, heterozygosity in the study species and other species in the study region, and resilience to disturbance. However, you don’t actually draw any conclusions or suggest what the level of genetic diversity your species exhibits might mean. This would be useful here in order to put your discussion on ‘Implications for restoration and management’ later on into context.

•	You will need to consider the role of animals on the transport of seeds or vegetative material, as this has been found in other seagrasses.

•	Discussion on cluster 3 is lacking. Why do the populations in cluster 2 group separately from those in cluster 3? I understand that your major talking point is the high genetic diversity and genetic differentiation between the Indian and Pacific Oceans, but the differentiation between cluster 2 and 3 is an interesting finding that is not discussed and should be.

•	Why did you only sample one population from the Indian Ocean? A more balanced sampling scheme would have given a better view of the overall picture.

•	The flow of the ‘Implications for restoration and management’ section is very poor and should be improved.

•	Following on from this – I do not think it is correct to be comparing genetic diversity estimates of plants and animals. Rather focus the discussion around other seagrass species – there are nunerous studies. Perhaps there are differences between tropical and temperate seagrass species that can be explored. This section requires rethinking. What does genetic diversity mean in the context of your sudy and why is it important? Detail this clearly.

•
•	Isolation by distance – you report a strong signal of IBD, yet this might be as a result of you carrying ot your IBD analyses across regions with known genetic breaks. Meirmans (2012) wrote a great paper “The trouble with isolation by distance” that details why a break in gene flow can inflate a signal of IBD. You should test for IBD within each of your clusters separately, rather than across clusters if that is possible.
Minor comments- mainly grammatical
Line 19: ‘regarded as a barrier that isolates organisms of the Indian and…’
Line 22: ‘organisms ‘ plural
Line 33: ‘in shaping the  genetic patterns of…’
Line 49-52: this sentence is a bit confusing and could be split up and clarified.
Line 53: ‘large land masses...’
Line 60 and 61: ‘populations’ plural, as you are talking about populations of different species
Line 61: Central rather than “middle”?
Line 63: ’a concordance in the geographical barrier…’
Line 67: ‘the Halmahera Eddy…’
Line 67: ‘are likely candidates shaping the biogeographic barrier…’
Line 72: Geological instead of ‘geographical’?
Line 74: divergence instead of ‘diversification’?
Line 78 ‘bivalves’ plural
Line 79: by ‘concordance’ do you mean they show the same pattern in terms of structure or genetic diversity, or do you actually mean that these populations are related/connected via gene flow. Please explain.
Line 83: ‘nuclear DNA markers…’
Line 84: missing full-stop after reference
Line 85: ‘using seagrasses is lacking.’
Line 89: ‘occurs’
Line 89: Include the common name for the species if you can.
Line 95: ‘fibrous strands (the remnants of old leaves).’
Line 96: ‘are capable of floating for up to 10.2 days…’
Line 98: ‘respectively (Lacap et al., 2002). This might limit…’
Line 99: ‘although, long distance…’
Line 100: ‘dispersal capacity…’
Line 102: ‘to find significant…’
Line 105: ‘used broadly in phylogeographic…’
Line 179: ‘NJ’ is this Neighbour joining? Either write out in full of define this abbreviation when you first introduce it.
Line 196-204: Maybe state why you are testing for deviation from HWE (you are testing whether your microsatellites are selectively neutral). Even though most analyses assume HWE, we know that HWE is not a realistic expectation (as you say, it can be influenced by population size etc.)
Line 216-221: Some repetition that could be removed.
Line 233: make the CT subscript.
Line 243: be more specific here. Did these studies look at a different region or different species?
Line 243-244: ‘The results presented here do not also reveal the…’ did you mean ‘do not only’?
Line 276: ‘all pairs of populations.’
Line 293: ‘NK, where the most geographically distant, showed distinct…’ rephrase this sentence, as it currently makes very little sense.
Line 295-297: you could say ‘Differentiation of the western Indonesian (Indian population) seems to be largely a result of…’ This acknowledges that there are other factors at play, such as current, which you discuss later.
 Line 310: forcing of genetic homogeneity? I understand what you are getting at but this needs further explanation
 Line 317: Try not to use ‘probably’ in this context. Rather say something like ‘it is possible that…’, ‘it is likely that…’ or ‘the seagrass may have…’
Line 320: how about ‘the alternating monsoon in Indonesia is also a possible confounding factor.’
 Line 333: this contradicts what you said earlier about currents acting as dispersal barriers and the low dispersal capacity of this species
Line 337: ‘ and a high level of genetic differentiation…’
Line 340: ‘local stocks’ are you referring to the entire Indo-Malay Archipelago or a specific site?
Line 345: Does seagrass with a higher level of genetic diversity provide ‘more’ ecosystems services or ‘better quality’ ecosystem services?
Line 349: ‘mate’ is not a good choice of words to describe plant sexual reproduction


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: STRONG GENETIC DIFFERENTIATION IN TROPICAL SEAGRASS ENHALUS ACOROIDES (HYDROCHARITACEAE) AT THE INDO-MALAY ARCHIPELAGO REVEALED BY MICROSATELLITE DNA
Review round: 1
Reviewer: 2

Output:
Basic reporting: To the best of my knowledge, this manuscript adheres to policies and templates. In my opinion, this topic is a valuable contribution to PeerJ and the authors do a sufficient job at explaining the relevancy of this research.

The manuscript contains extensive grammatical mistakes that must be fixed. I am assuming these arise from the fact that the authors are writing English as a second language. The good news is that these mistakes are primarily tense-based (noun or verbs that should switch from plural-singular or vice versa) and minor spelling errors. I found very few sentences that were unclear or ambiguous in meaning despite these errors. I recommend the authors run this manuscript through a word processor with an English spell/grammar check such as Microsoft Word and work with PeerJ or a native English-speaking colleague to review the manuscript explicitly to correct these mistakes. In this review, I limit my suggested changes to the abstract as an example:

Line 19 – “ is regarded as [a] barrier that isolates organism[s] of [the] Indian and”
Line 20 – “biota from [this region] have found”
Line 21 – “, seemingly dependent on [] taxon and [] methodology. The [g]enetic “
Line 22 – “marine organism[s] in [this region] are related to several”
Line 23 – “ Shelf[] and recent physical”
Line 28 – “Both a [neighbor joining] tree based on”
Line 29 – “ E. acoroides.[] Further, AMOVA revealing significant partition[ing] of”
Line 32 – “such as [the] South Java Current and [the] Seasonal[y] Reversing”
Line 33 – “in shaping genetic pattern[s] [in] E. acoroides.”

Other basic reporting on the body of the manuscript:

Line 49-52 “Although several phylogeographic studies…from both oceans.” This sentence is unclear and needs to be reworded. Are the authors trying to say that only a few studies have tried to identify specific elements in the region that promote genetic structuring? The term “overlapping region” is not good here.

Line 79 – phylogeographic DIScordance?

Line 107 – these markers are co-inherited (not co-dominant, since they are not expressed)

Line 184-187 – this 3-sentence paragraph begins and ends with sentences ending with “used for further analysis” I recommend the authors change the first to “were discarded after initial examination” or something similar so that the sentences are not so repetitive.

Line 200-201 – “However, according to Micro-checker…null alleles” This sentence is unclear and needs to be reworded for clarification. As a side note which I will bring up again, this sentence is the only reported result from running Micro-checker and I recommend more information is provided.

Line 326-327 – inconsistent correlation between genetic and geographic distance for KJ and ANS? Where is this information? There are no details about this in either the IBD figure or the results section.

Basic reporting on figures & tables:

Figure 1 – I recommend putting an “Indonesia” label on the small inset and perhaps placing a simple box around the zoomed area so that readers not familiar with this area can orient themselves.

Figure 2 – Negative geographic distance is impossible. The x-axis should start at 0. Along with other comments that will follow, I think that Nakuri comparisons should be removed from this figure and that comparisons between sites of different clusters (2 & 3) should be filled (e.g. gray circles instead of open ones) so that we can see how this correlation is affected by genetic clustering.

Table 1 – This table lists the number of individuals collected at each site but the authors should also include how many of these individuals were successfully genotyped at the 6 loci used (unless they had success for all samples, in which case they should mention that somewhere in the manuscript).

Table 3 – As is, there are only site-by-site data. Are the alleles found at each site unique? Or are alleles of different loci shared among sites. This table should also include the total number of alleles at each locus. I also recommend putting all pre-corrected significant deviations from HWE in bold and using an * (asterix) to denote with ones were still significant after correction.

Table 4 – Nowhere in this manuscript are the actual geographic distances between sites reported. The upper-diagonal ***  is a little unnecessary since all sites were significantly different from one another. This can simply be reiterated in the table legend. I suggest replacing the upper-diagonal with geographic distance.
Experimental design: To the best of my knowledge, this work is well within the scope of research published by PeerJ. The authors do a good job of defining their research questions, and their study species and sampling design is appropriate and relevant.

Methods:

A kit was used for the first multiplexed reaction of 5 primer sets, but individual reagents were used in the second reaction of 3 primer sets. I recommend reporting concentrations along with volumes for primers, dNTPs or other reagents not tagged by supplier (i.e. concentration not need for the Amplitaq Gold/buffer from Applied Biosystems) for this second set so that these methods can be replicated.

Line 138-139 “GeneScan 500 LIZ…line standard.” I recommend moving this sentence in front of the one previous to keep the order chronological since size standards are added before sequencing occurs.

Data Analysis:

The greatest issue I have with the manuscript as it stands now is whether or not the 6 loci successfully amplified are neutral markers or influenced by some sort of selection. I am not confident that the authors have fully explored the data from these loci to properly determine whether these are markers that are neutral (and therefore useful in assumptions regarding passive seed transport and gene flow) or whether these markers are linked to sites that may be under selection and are therefore under the influence of local adaptation.

The red flag which makes me very closely examine the analyses of the authors is that when they ran pairwise Fsts, every site is significantly different from every other site. This could be an entirely true phenomenon based on highly restricted dispersal. But, this could also be a false signature driven by one or two of their 6 loci that might be influenced by selection or other issues that arise with a problematic locus (allelic dropout, etc). To address this issue, I suggest the authors start with the following:

1. The authors applied a very conservative method of correcting their p-values (Holm Bonferroni) for HWE tests which left anything with a p-value of < 0.000 significant (2 tests). When I played around with using the Benjamini-Hochberg (1995) method of correcting FDR on the author’s p-values (a method shown to correct for type I error while  creating fewer type II errors), any p-value < 0.0065 remained significant (5 tests). Additionally, using the Holm Bonferroni method at each locus (m=7 instead of m=38/42) the same 5 tests remained significant. These five significant tests are linked to two loci. At the very least, the authors should re-run their analyses without locus Eaco_054 for which 43% of sites (3 of 7) are out of HWE using these methods of correction.

2. The authors ran Micro-checker, but the only results were reported in a single, unclear sentence (Line 200-201). What were the results? Which loci had evidence of null alleles or scoring errors? Do any issues arise in loci Eaco_001 or Eaco_054 where there is evidence of deviation from HWE?

3. The authors use a post-hoc AMOVA which is really somewhat superfluous. AMOVAs are designed to be used to test a priori hypotheses. Running an AMOVA using clusters that have already been determined using other analysis methods is redundant. I suggest that the authors remove their post-hoc AMOVA and instead, run a locus-by-locus AMOVA to see if whether there are any loci driving the genetic structuring they have measured between sites. If they find that a particular locus is driving all of the between-site differences, that locus will need to be evaluated for robustness.

4. Report the total number of alleles found at each locus. Having this data is helpful in evaluating the validity of loci. Only loci with shared alleles are useful in population genetic analyses.

The other major issue I found is with the IBD analysis. Correlations between geographic distance and genetic differentiation will be highly biased by hierarchical genetic structuring (see Meirmans 2012- The trouble with isolation by distance). With their neighbor-joining and Structure analyses, the authors have detected the kind of genetic clustering that will bias an IDB analysis. Given the scale of its genetic and geographic distance from all other sites, the authors should remove Nakuri from any IBD analysis (I suspect that removes the 6 most upper-right points). In addition, it would be a very good idea to distinguish the points that represent comparisons between sites in the Java Sea belonging to different Structure clusters (see my comment on Figure 2). If the correlation is being driven by these points, then there is actually no evidence for IDB, only genetic clustering.
Validity of the findings: The validity of the author’s findings and restoration/management implications are not fully supported until they address the issues I have discussed previously (particularly the issues with their loci). The author’s hypotheses for their results are heavily dependent on currents and oceanography, which are only truly examined using neutral genetic markers. While I suspect there will be no change in the genetic differentiation of Nakuri from the other sites, whether the genetic structuring they have found in the sites in the Java Sea proves robust and whether it is appropriate to conclude that it is likely current-influenced instead of a sign of local adaptation is dependent on further analysis of their loci.

Other notes on the Discussion:

Lines 256-260 – variance in genetic diversity is also highly effected by sample size

Lines 326-327 – what is this? There is nothing in the results as to how KJ and ANS show an inconsistent correlation between genetic/geographic distance. Provide more detail and explain.
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: STRONG GENETIC DIFFERENTIATION IN TROPICAL SEAGRASS ENHALUS ACOROIDES (HYDROCHARITACEAE) AT THE INDO-MALAY ARCHIPELAGO REVEALED BY MICROSATELLITE DNA
Review round: 2
Reviewer: 1

Output:
Basic reporting: The basic reporting has been much improved and the authors have addressed all previous comments. However, there are still some shortcomings that the authors need to address before the MS can be published.
Experimental design: improved.
Validity of the findings: The findings are valid.
Additional comments: L51: coalesced
L55: and frigate tuna
L62: need a reference for currents as provide reference for geological history. On that note, evolutionary, rather than geological, is correct
L62 – 71: this paragraph should be written slightly. It deals with both geological/evolutionary history of a region, but also the oceanography. To me it makes sense that historical effects are listed first and then maintained by contemporary processes. It would make it clearer if you wrote this paragraph in that order.
L90: and the rhizomes
L92: 10.2 days?
L93:the distances are unclear
L97: I disagree that the term ‘philopatric’ is appropriate for seagrasses. The term is more commonly used for animals and suggests a choice of staying or returning to a particular habitat, which seagrass seeds or suckers do not have.
L104: delete of
L111” what is ‘genet’?
L147: Micro-checker does not have a hyphen
L246: there is a whole section on genetic diversity here, and you mention that one of the major aims of the paper is to describe patterns of genetic diversity in this species. However, in the introduction the focus is on the historical and contemporary biogeography of this species without a mention of genetic diversity. This needs to be rectified. Ideally you would place this into a broader context of why genetic diversity is important, particularly in species that potentially have low dispersal (even though it seems from your study that even distantly situated populations are connected), i.e. reduced gen div at edge populations, more inbreeding etc. This is an important aspect.
L256: you show that genetic diversity is similar for your study to previous ones – what does that mean for this species? Good? Not so good?
L266: you need to build on this last sentence. At present this section is very descriptive and comparative. See my previous comments on why you need to investigate and better integrate a discussion on gen div.
L271 onwards: this is very confusing. You say that there is high structure, but then previously in L221 you say that samples separated by over 1000km are closely related? Which is it? Is the relationship between KJ and ANS different and why?
L365: lost
L367: above average is relative. Relative to what?
L376: there is a word missing here
L379: I think what is worth mentioning here that despite the loss of seagrass habitat, these plants manage to maintain good genetic diversity and heterozygosity. Should be noted.

References: there are numerous editorial issues with the references. Please ensure that you check these carefully. An example is L564: Molecular Ecology


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: STRONG GENETIC DIFFERENTIATION IN TROPICAL SEAGRASS ENHALUS ACOROIDES (HYDROCHARITACEAE) AT THE INDO-MALAY ARCHIPELAGO REVEALED BY MICROSATELLITE DNA
Review round: 2
Reviewer: 2

Output:
Basic reporting: The English is much improved with only a few minor errors which have been noted by line in the GENERAL COMMENTS section. The introduction provides good context for their particular study region and species.
Experimental design: The research is meaningful, methods and experimental design are clear.
Validity of the findings: The authors have clearly put a lot of effort into the improvement of this manuscript. There are three issues that need to be addressed in this version. These issues can be fixed with relatively small additions or modifications to their analyses and discussion.

1. IBD. The authors are moving in the right direction with the changes to their IDB analysis. However, their conclusions regarding the results remain wrong. They consistently state in the results, discussion, conclusion that there is significant IBD among all sites in E. acoroides. However, the data they present indicate that there is no IDB, only distinct hierarchical clustering. If one lumps two (or three) geographically distinct genetic clusters into one group and runs an IBD analysis as the authors have, the clustering will bias the results (creating a false positive). If the authors wish to run two or three of their clusters together in an IBD analysis, they need to use something like a partial mantel and test the correlation of genetic and geographic distance against a z-matrix of pairwise cluster associations (in other words, a third matrix of pairwise relationships where pairs are coded as either belonging to the same cluster, 0, or different clusters, 1). See Meirmans et al. 2012 for discussion of interpreting IDB results when hierarchical clustering is present. I don’t believe IBDWS is capable of running a partial mantel, however, there are several r packages that can.

The mantel test within cluster 2 is properly run and interpreted.

2. Issues with Eaco_054. In their response to previous review, the authors state that they reran their Fst analysis excluding Eaco_054 and they still generated significant p-values. I suggest they report that they did this in their manuscript and show the Fst table for the analysis without Eaco_054 with FDR corrected p-values in their supplemental material to support their results. The reason I suggest this is two-fold. 1) this locus deviates from HWE after FDR correction in 3 out of the 7 locations and 2) the total number of alleles at this locus is 29, which is more than the sample sizes at 3 locations and only 1 less than the sample sizes at 2 other locations. By this account, Eaco_054 is too polymorphic relative to sample size to be an ideal locus for population analysis. I feel it is important to show within their manuscript that its presence or absence makes no significant difference to their results.

3. The paragraph in lines 257-268 should be revised. Observed heterozygosity is LARGELY impacted by the researcher’s selection of markers. For example, here, the authors threw out a marker with Ho = 0 (Eaco_052) and do not report it in their estimates of Ho.  They are correct to do so since it will be non-informative in population structure analysis, but it still exists. If the authors wish to discuss comparisons of Ho, they need to stick with comparisons between species or localities that have been analyzed with the same msat loci that they used.
Additional comments: Clarity:

Line 75 – This sentence comes across unclearly. I suggest changing it to something like, “These studies have found concordant phylogeographic breaks between populations in the Indian Ocean and Java Sea.“

Minor grammatical issues:

Line 51 – coalesce to coalesced

Line 58 – mangroves to mangrove

Line 64 – barrier to barriers

Line 75 – in Indian to in the Indian

Line 90 – rolled, the to rolled, and the

Line 93 – 0.1 63.5 km to 0.1-63.5 km

Line 102 – marker to markers

Line 104 – pattern to patterns

Line 148 – and 95% a confidence level to a 95% confidence level

Line 163 – population to populations

Line 171 – 100,000 steps of Markov Chain Monte Carlo (MCMC). to 100,000 steps of Markov Chain Monte Carlo (MCMC) sampling.

Line 197 – After correction for multiple test, to After correction for multiple tests,

Line 356 – becoming loss to declining (or something similar)

Line 391 – result also indicated to results also indicate


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: STRONG GENETIC DIFFERENTIATION IN TROPICAL SEAGRASS ENHALUS ACOROIDES (HYDROCHARITACEAE) AT THE INDO-MALAY ARCHIPELAGO REVEALED BY MICROSATELLITE DNA
Review round: 3
Reviewer: 1

Output:
Basic reporting: Good. The major issue with this version is grammatical errors in newly added sections. See Comments to the author.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Broad comments:

Fix your subsection numbering throughout the manuscript. (For example, Lines 116-117. The section number is 3, but the subsections are numbered 2.1, 2.2 etc.)

Check for consistency in the term isolation-by-distance across the manuscript. There are instances of “isolation by distance,” “isolation-by-distance,” and “Isolation By Distance.” I recommend changing them all to “isolation-by-distance.”

The authors have made several changes to their discussion. I found that these changes really strengthened the discussion of their results, however, it appears that the new discussion sections have the same grammatical issues that were present in earlier versions of the manuscript, and at this point fixing those is the largest thing that needs to be addressed in this manuscript. I spent time going through each section making comments and suggestions to assist with this.

In addition, if the authors use a location name in the manuscript, that location should be labeled in one of their figures. For example, Kalimantan is used in the discussion section, but the island is labeled only Borneo in the figures. Other locations discussed but not specifically labeled also include the Malaka Strait.

Grammar or other issues by section:

Abstract

LINE 26: remove comma after “taxon”

Introduction

LINE 42: remove comma before “seemingly” and remove comma after “Although”

LINE 45: change “genera” to “genus” and remove comma before “and”

LINE 57: change “population structures” to “population structure”

LINE 58: I recommend changing “simple” to “homogenous”

LINE 61: change “Euthynus” to “Euthynnus”

LINE 104: change “continue” to “continual”

LINE 113-114: “and infer on the effect of the Sunda Shelf and ….” is awkward. I recommend changing to something like “and to infer how the Sunda Shelf and regional currents shape the genetic patterns found in this species”

Materials and Methods

LINE 179: change “used Mantel test” to “used a Mantel test”

LINE 187-188: change “Both Mantel and partial Mantel test was performed” to “Both Mantel and partial mantel tests were performed”

Results

LINE 196: change “the Eaco_050” to “Eaco_050”

LINE 209-211: change “revealed five loci (…) that deviated from” to “revealed that five loci (…) deviated from”

LINE 212:  change “prior to multiple test” to “prior to a multiple test”

LINE 223: change “FST test” to “FST tests”

LINE 224-226: I recommend changing “; our findings were not different between datasets (…) Therefore, all loci” to something like “Removing Eaco_054 did not change the results of pairwise comparisons (…), therefore all six loci were included in further analyses. ”

In addition to the above comment, I noticed that Supplemental Table S1 was the raw allelic data for each individual, not the results of tests of pairwise differentiation. So I recommend removing the reference in the above sentence and adding a sentence at the end of this paragraph along the lines of: “Individual genotypes for these loci are reported in Supplementary material, Table S1.”

LINE 230: change “highly significant” to “significant” (with p-values, results are either significant or not, there are no levels of significance).

LINES 231-232: change “highest” and “lowest” to “largest” and “smallest”

LINES 246-247: I recommend changing  “After performing partial Mantel test, the IBD result still remained significant with P=0.03 (Fig.3).” to “A partial Mantel performed on the remaining Java and Natuna Sea locations indicated that IBD is present across these sites (p=0.03, Fig. 3).”

Discussion

LINE 251: change “number of alleles) genetic” to “number of alleles), genetic”

LINE 266: remove the comma before “and”

LINE 269: change “heterozigosity” to “heterozygosity”

LINE 270: can this personal observation be attributed to a specific author or authors on this manuscript? If so, I recommend using “ (pers. comm. Author Name(s)).”

LINE 271: change “area are tend” to “areas tend”

LINE 272: change “heterozigosity” to “heterozygosity”

LINE 271-273: The sentence “Although ANS… undisturbed area.” is awkward. I recommend changing to something like “Although ANS had the lowest observed heterozygosity (Ho), sampling at this location was also conducted in an undisturbed area so the lower Ho may be the result of other factors.”

LINE 273-274: This sentence is awkward. I recommend changing to something like “Microchecker results indicated that ANS had an excess of homozygosity, a potential indicator of inbreeding.”

LINE 275: change “occur” to “occurs”

LINE 275: change “reduce” to “reduces”

LINE 286: change “in Indo Malay Archipelago” to “in the Indo-Malay Archipelago”

LINE 289: remove comma before “and”

LINE 300: change “a result of” to “due to” so that the word result is not used twice in this sentence

LINE 310: change “seed” to “seeds” and “does” to “do”

LINES 315-316: change “Although, clustering output also showed that there were any secondary peak” to “Clustering output indicated secondary peaks”

LINE 316: I recommend changing “This results implied…major groups.” to “These results indicate the presence of further substructure similar to that found in FST analysis.”

LINE 318: change “TD and PR. While at K=7” to “TD and PR, while at K=7”

LINE 332: change “Euthynnus affin” to “Euthynnus affinis”

LINE 337: change “scale” to “scales”

LINE 341-342: change “this study, mirrors the genetic structure of genus” to “this study mirrors the genetic structure found in the genus”

LINES 345-346: change “found an appropriate habitat across Seribu Islands, Bangka, Batam and used it as stepped stone to a long distance dispersal.” to “found appropriate habitat across the Seribu, Bankga, and Batam Islands and used these islands as stepping stones for long distance dispersal.”

LINE 353: change “across Java” to “across the Java”

LINE 357: change “result” to “results”

LINE 359: change “find” to “found”

LINES 360-361: change “This genetic pattern probably influenced by sea level changes during Pleistocene” to “This genetic pattern may also have been influenced by sea level changes during the Pleistocene”

LINE 363: change “seemed” to “seem”

LINE 364: change “this connection could be facilitated the gene flow” to “this connection may have facilitated gene flow”

LINE 365-366: change “creating” to “create” and “maintaining” to “maintain”

LINE 367: change “maintenance” to “maintain”

PARAGRAPH 359-370: This paragraph is a very good inclusion but I feel like the last two sentences need to be deleted. They are not specific to the paragraph topic and the citations used are found in other places in the manuscript. The beginning of the paragraph is good – a shifting coastline that at one point included two contemporary (and distant) island habitats while sea levels rose and the Sunda Shelf was flooded is a good hypothesis for the genetic patterns the authors found in the Natuna and Java Seas. However, long distance dispersal via hurricanes or typhoons that might have specifically affected only those two islands and not the other sites sampled in this region is not helpful or a particularly strong explanation for the author’s findings. The beginning of this paragraph could possibly be combined with the following paragraph.

LINE 371: change “Seagrasses population in Natuna seas could be originating from any different source.” to “Seagrass populations in the Natuna Sea could be originating from a different source.”

LINE 372: change “area in Natuna Sea is supplied by a larval transport from South China” to “areas in the Natuna Sea are supplied by larval transport from the South China”

LINES 373-374: change “Although, others study showed that population in Natuna might also come from the Andaman Sea via Malaka strait following the ice retreat” to “Other studies showed that populations in the Natuna Sea may also receive propagules from the Andaman Sea via the Malaka Strait following the ice retreat”

LINE 375: change “population” to “populations” and “guess” to “suspect”

LINE 376: change “barrier” to “barriers”

LINE 377: change “part of Natuna Sea” to “parts of the Natuna Sea”

LINE 378-379: change “to reveal the origin ” to “to better understand the origins of the populations”

LINE 379: change “Malaka strait and South China Sea” to “the Malaka Strait and the South China Sea”

LINE 383: change “organism” to organisms”

LINE 384: change “ecosystem” to “ecosystems”

LINE 386: change “ have been conducted” to “is underway”

LINE 391: change “Structure” to “Bayesian”

LINE 391: change “recommend at least there are three” to “recommend resource managers treat populations across our sampling region as three”

LINE 392: change “to maintain unique genetic characteristics of the region for seagrasses conservation” to “to maintain the unique genetic characteristics of each region to support seagrass conservation”

PARAGRAPHS 389-398 and 399-405: The information in these two paragraphs should be combined into a single paragraph. There is a lot of redundancy between them.

PARAGRAPH 406-415: I recommend the first sentence in this paragraph be moved to an appropriate place in the proceeding paragraph(s), and the last part of this paragraph should be moved down to the Conclusions section.

Conclusion

LINE 418: change “heterozygosities between” to “heterozygosity in”


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: REPETITIVE LOW INTENSITY MAGNETIC FIELD STIMULATION IN A NEURONAL CELL LINE: A METABOLOMICS STUDY
Review round: 1
Reviewer: 1

Output:
Basic reporting: Low intensity repetitive transcranial magnetic stimulation (LI-rTMS) was found recently as a beneficial way to treat depression, pain, and probably other neurological problems. The LI-rTMS is a non-invasive form of brain stimulation that induces structural and functional brain plasticity. However, the mechanisms by which this magnetic stimulus affect the brain, and the potential for LI-rTMS to promote axonal regeneration following neurotrauma has not been investigated yet. Here the authors used a rat neuroblastoma cells to follow the effect of LI-rTMS at a cellular and biochemical level. They found that LI-rMS reduces selected metabolites shortly after stimulation, without affecting the main energy supplies. The effects were frequency-specific with 1 Hz stimulation having stronger effects than 10 Hz. Overall, this is a well written and interesting study that provides novel insights into the modulation of neural tissue by LI-rMS. However, the scope of the article is somewhat limited, and suggestions how to expend it as well as a few minor comments are as follows:
1)	The effect of LI-rTMS on metabolites is well presented, and the findings are important and deserve publication. However, in my mind, the system of B50 cells has a much wider potential in studying the mechanisms by which the magnetic field is sensed by the cells (what is the antennae that absorbs it), what are the signaling moieties involved (AMPK? mTOR? Calcium?) and what other physiological effects (e.g. morphology, proliferation, migration) are influenced. If the authors feel that these points are out of the scope of this article, they should at least discuss them under “Discussion”.
2)	The logic of Figure 2 is not clear to me, and should be better explained. Can the authors specify the metabolites measured in each point?
3)	In figure 3, it would be beneficial to add where is the suspected point of LI-rTMS interference. In addition, it is suggested to increase the font, so that the names of the metabolites become clearer.
Experimental design: The authors used a rat neuroblastoma cells to follow the effect of LI-rTMS at a cellular and biochemical level.
I have no problem with this design.
Validity of the findings: The results seem to be valid.
Additional comments: 1)	The effect of LI-rTMS on metabolites is well presented, and the findings are important and deserve publication. However, in my mind, the system of B50 cells has a much wider potential in studying the mechanisms by which the magnetic field is sensed by the cells (what is the antennae that absorbs it), what are the signaling moieties involved (AMPK? mTOR? Calcium?) and what other physiological effects (e.g. morphology, proliferation, migration) are influenced. If the authors feel that these points are out of the scope of this article, they should at least discuss them under “Discussion”.
2)	The logic of Figure 2 is not clear to me, and should be better explained. Can the authors specify the metabolites measured in each point?
3)	In figure 3, it would be beneficial to add where is the suspected point of LI-rTMS interference. In addition, it is suggested to increase the font, so that the names of the metabolites become clearer.


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: REPETITIVE LOW INTENSITY MAGNETIC FIELD STIMULATION IN A NEURONAL CELL LINE: A METABOLOMICS STUDY
Review round: 1
Reviewer: 2

Output:
Basic reporting: Paper adheres to all basic reporting requirements.

Minor note: references need to be rechecked
Eg: some paper titles all start with capitals, others do not. Some journal titles are given in abbreviated form (line 308). Check page numbering (line 393)
Experimental design: 1) The analytical method of choice – GC-MS – is a highly sensitive platform, able to produce 100’s of identifiable peaks. From this study: “Based on GC-MS profiling, a total of 18 reproducible intracellular metabolites were identified from the total ion chromatograms (TIC)”. Why were only 18 metabolites identified? On what basis is ‘reproducible’ used/defined as here? Were there data reduction steps taken? More description of the data-processing is required.

2) In the methods: “The supernatant was evaporated before adding 500 μl of water and freeze-drying again.” – what was the point of adding the water and freeze-drying again? Especially immediately before the derivatization steps as any trace of water reverses derivatization.
Validity of the findings: 1) The hypothesis generated from this study is built around the following statement: “observed depletion of metabolites was consistent with an increase in GABA release as a result of higher spontaneous activity”. Yet, GABA levels are not quantitatively shown/given in the paper – the statement that GABA increases needs to be backed up by empirical proof.

2) The abstract is inconsistent with the main text. The groups in the abstract are stated as: “We delivered LI-rMS (10 mT) at 1 Hz and 10 Hz (n=5 wells per group)”. In the legend for Figure 2 & Table 1, the groups are stated as: “cells stimulated with LI-rMS at 1 Hz (n=4), 10 Hz (n=6) and unstimulated controls (n=6)”. Number of wells per group is not given in the main text.

3) Regarding number of wells per group – six, let alone four (as given for 1Hz in figure 3 and table 1), is a very low number (n) to be using for statistical analysis. A main pillar behind basic statistics is that a large(r) sample size will give more reliable results – an indulgence not often affordable in a typical metabolomics study. Should the study conduct research with an extremely small sample size (n ≤ 5), the t-test can be applied, as long as the effect size is expected to be large [see: De Winter, J.C., 2013. Using the Student's t-test with extremely small sample sizes. Practical Assessment, Research & Evaluation, 18(10)]. Often the Cohen’s d effect size is used, with cut off values of small (d = 0.2), medium (d = 0.5) and large (d ≥ 0.8) [C. Carson, The effective use of effect size indices in institutional research. Citováno dne, 11, 2016]. Hence, for a small sample size, a low p-value (p<0.05) combined with a high d-value (d>0.8) is recommended as an indicator of being univariately significant.

4) In line with the comment above – what are the cut-off values for the F-statistic given in Table 1? No mention of the F-statistic is described in the text (reporting, results, nor discussion), and why was this statistic (not commonly used in metabolomics) used as a statistical measure for metabolite selection? Similarly, what is the cut-off value for significance with regard to the fold change? GC-MS is quantitative – means, standard deviations and ranges would add value to Table 1? This, and the previous comment, is aimed at helping to improve upon Table 1 and the reporting of the quantitative univariate measures from the metabolomics data.

Minor note: oxalosuccinate is a highly unstable intermediate that immediately undergoes decarboxylation to 2-ketoglutarate. Hence, oxalosuccinate is not typically shown as an intermediate in the TCA cycle. Oxalosuccinate is not important in this study; hence it seems out of place in Figure 3.
Additional comments: This is a well-designed study that examines the effects of electromagnetic stimulation of brain cells, specifically neuroblastoma cells. The therapeutic applications of electromagnetic stimulation of the brain holds much potential. Studies such as this will help expand our understanding of how and what is occurring at the metabolic level. While adequately covering the need for such a study, the reporting of the metabolomics aspect here still needs to be improved upon (see other 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: CHLOROPID FLIES (DIPTERA, CHLOROPIDAE) ASSOCIATED WITH PITCHER PLANTS IN NORTH AMERICA
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: This paper is well illustrated, problem well defined and researched. Most of my comments and corrections are added to the pdf version of the ms. In addition, I have the following points:

1. Jones (1916) also described the immature stages of Aphanotrigonum darlingtoniae, but this was not mentioned in the ms. This should be added. Also, the immature stages were reviewed in the following reference (Johannsen, O.A. (1935) Aquatic Diptera. Part II. Orthorrhapha-Brachycera and Cyclorrhapha. Cornell University Agricultural Experiment Station Memoir 177: 1-62, pls 1-12.). This reference should also be added to the ms.

2. The link to the Jones notes could be more precise and direct. I suggest that you use the link to the "Insect Associates" page.

3. Jones (1916) actually did not designate a holotype. He states "types male and female" and lists paratypes. This actually does not constitute a holotype designation and all specimens are syntypes. The USNM type number is not unique and according to the ms, the number is present on more than one specimen. The type labels were added by curators at the USNM following publication and the holotype label is not valid (but this specimen can certainly be used for the lectotype). A lectotype designation is required and recommended here. Also did you examine the "paratypes" in the other collections, i.e., at ANSP?


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: CHLOROPID FLIES (DIPTERA, CHLOROPIDAE) ASSOCIATED WITH PITCHER PLANTS IN NORTH AMERICA
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall a very well-written and informative piece of research. Excellent coverage of background information and context for natural history of species discussed and described. One minor suggestion would be to include a brief discussion of the known diversity and geographic range of the 2 genera containing pitcher plant associated species of Chloropidae, simply to provide further context for the rarity of this associative life history and potential inspiration for field naturalists to watch for other associations in their travels.
Experimental design: Well defined and articulated. Article and new species are registered with the ICZN Zoobank database, and LSIDs are provided along with PeerJ's required text on digital publication of new names.
Validity of the findings: No comment.
Additional comments: A well-written and engaging piece of research, and a touching tribute to a Canadian leader in Dipterology and taxonomic entomology. A few minor typos or suggestions for grammatical refinements are provided as comments in the attached PDF, but otherwise a very clean and clear manuscript.


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

Input:
Title: CHLOROPID FLIES (DIPTERA, CHLOROPIDAE) ASSOCIATED WITH PITCHER PLANTS IN NORTH AMERICA
Review round: 1
Reviewer: 3

Output:
Basic reporting: This paper is written in clear English, it is well referenced and relevant. The figures are relevant and of high quality. This is a description of a new species, therefore no raw data exists.

The BOLD data for the two described specimens of Aphanotrigonum darlingtoniae could not be accessed as it is not publicly available. However, it seems to be uploaded to BOLD, but I am not an expert in this system.

I could not find the new species data in Zoobank, but I am not an expert on this system and might have done something wrong.
Experimental design: It is a new species, therefore fills a knowledge gap. The author has investigated the subject to a high standard and the methods are appropriate and can be replicated. The information provided is sufficient.
Validity of the findings: The conclusions are well stated and the paper is of a high standard.
Additional comments: This paper includes the description of one new species and it is very useful that a comprehensive re-description of a second species is included. It is a valuable contribution to the knowledge of Chloropidae associated with pitcher plants.
I could not find the specimens in BOLD or zoobank and I suggest to correct this, but I am not an expert in these systems, so might have done something wrong.
I found some small typos in the ms as follows:
line 181 - land should be and
line 182 - ines should be lines
line 186 - pollnose should be pollinose


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: CLINICAL IMPACT OF ALBUMIN IN ADVANCED HEAD AND NECK CANCER PATIENTS WITH FREE FLAP RECONSTRUCTION—A RETROSPECTIVE STUDY
Review round: 1
Reviewer: 1

Output:
Basic reporting: In this study, the authors aim to determine the prognostic value of serum albumin level among 233 patients with advanced head and neck squamous cell carcinoma (HNSCC) were diagnosed with HNSCC and underwent surgical resection of tumor with microvascular free flap reconstruction simultaneously between January 2009 and December 2011 in Kaohsiung Chang Gung Memorial Hospital, Taiwan. I think that the manuscript might be interesting for the researchers who are mainly interested in head and neck cancer. In general, the manuscript is clearly written and the tables are well organized. However, the paper needs some additional works, in particular the statistical methods parts, and some minor changes are recommended before considering the paper for publication.
Experimental design: My concerns are as follows:

In abstract,

	In Line 25-28: Please provide details for statistical methods in methods section of the abstract.

In materials and methods, statistical analysis

	In Line 91-102: The authors also did not provide which normality test they used to check the normality assumption of the data. The following normality tests, such as Shapiro-Wilk test, Kolmogorov-Smirnov normality test or Anderson-Darling test can be thought to assess normality.

	In Line 92: Please change “SPSS 20.0” to “IBM SPSS Version 20.0”.

	In Line 95-96: Student’s t-test was used to compare the means of independent samples. Thus, the sentence “An independent sample t-test was used to analyze the length of hospital stay after surgery.” should be corrected. For example, authors can use “An independent sample t-test was used to compare the mean length of hospital stay after surgery for two patient groups of postoperative albumin levels (≥3.5 versus <3.5)”.

	In Line 128: The authors mentioned that they used chi-square test, univariate and multiple regression analysis. However, they did not provide these tests in the “statistical analysis” part. Please update this part.

In Table 1,

	Please change “Median Age [range] (year)” to “Median Age (year) [range]”.

	Please change “Median follow up time [range] (year)” to “Median follow up time (year) [range]”.

	Please recalculate the percentages of “recurrent site”, because the total number of these values does not equal to 100%. Use total number of recurrence (75 cases) to calculate these percentages rather than 233 cases. In addition to this, please correct the recurrent site of the patient (no:106) as “local” in raw data. Then, the total number of local recurrent site will be 26 as in Table 1.

In Table 4,

	The table 4 may be removed, these findings can be interpreted in the results part.
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: CLINICAL IMPACT OF ALBUMIN IN ADVANCED HEAD AND NECK CANCER PATIENTS WITH FREE FLAP RECONSTRUCTION—A RETROSPECTIVE STUDY
Review round: 1
Reviewer: 2

Output:
Basic reporting: The study is about the determination of the prognostic value of the serum albumin level for the patients with advanced HNSCC (head and neck squamous cell carcinoma) undergoing surgery with simultaneous free flap reconstruction. In the analyses, the authors use the multiple regression to find the relation between  clinical factors and postoperative major wound infection.

Regarding the  analyses and associate conclusion, I consider that the article can be published once the listed suggestions will be made.

On the other side, I think that the problem is well-defined and literature is enough to cite the previous works.
Experimental design: The experimental set-up is well-defined and related works are listed. Whereas I consider that the analyses should be renewed partially. Because in the analyses, the authors directly use pairwise p-value between each clinical factor versus postoperative major wound infection (Table 2). But the interrelation between each clinical factor is not be considered. I think that the correlation  between factors should be computed initially. From the results, if a high multicollinearity is observed, the analyses should be revised based on the independent variables (i.e., factors).  Furthermore, the authors use the univariate analysis. But I think that all factors should be taken as predictors and the response is chosen as postoperative major wound infection under the multiple regression as long as the assumptions of this model are checked. Then the significance of this big model (each predictor in the model) can be evaluated for their significance. Here, if the assumptions of the multiple regression cannot be maintained, its non-parametric version can be applied too.

Moreover, I think that rather than the individual t-test, the Bonferroni corrected t-test can be used as the analyses are done under simultaneous effects of all risk factors.
Validity of the findings: Regarding the suggested analyses in Section 2, the results can be renewed.
Additional comments: None


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

Input:
Title: CLINICAL IMPACT OF ALBUMIN IN ADVANCED HEAD AND NECK CANCER PATIENTS WITH FREE FLAP RECONSTRUCTION—A RETROSPECTIVE STUDY
Review round: 2
Reviewer: 1

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


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

Input:
Title: THE ANATOMY OF THE FOVEOLA REINVESTIGATED
Review round: 1
Reviewer: 1

Output:
Basic reporting: The background is clear and sufficient.
The aim is relevant and according with the procedures.
Experimental design: Research question is clear and important.
methods are well presented, and are of high quality.
Ethical aspects are well explained.
Validity of the findings: I Consider they showed interesting and meaningful results. But presentation can be improved.
Additional comments: The authors analyzed the structure of primate foveola and correlate it with the Stiles Crawford Effect of the first kind (SCE). They followed electron microscopic studies as well as ion beam/scanning electron microscopy and shown elegant 3D images. The results support the hypothesis that the anatomy of the foveola result in the SCE effect.
The field background is good. The results are interesting and propose that Müller cells might participate in the SCE.
However, I consider some points should be taken in account previous to be accepted for publication.
1.	All the results should be presented in the corresponding section; then, lines 290-305 (discussion) should be at the result section. Following that, the figures (supplemental and videos) must have a sequential order (1-7, not 1,4,6…). Also, suppl. figure 1 represent the principal anatomic results, so should not be supplementary.
2.	Please check the figures, I could not find panels E and F in Fig. 2.
3.	Legend of Fig.3 should be modified according with the panels and each one explained, indicating the meaning of the different symbols.
4.	Line 290, the measurements obtained in this work must be presented in the result section.
5.	The size of the figures, particularly the S1, is not sufficient to identified the type of cells indicated. There is possible to identified Müller cells with an specific antibody?
6.	Since the cones were found to be curved, that can also participate in the SCE, please discuss.

Minor comments:
1.	Line 118, indicate type of fixative.
2.	Line 271, reference is not complete.


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 ANATOMY OF THE FOVEOLA REINVESTIGATED
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper is clear and unambigous, all the Literature references needed are included, with professional structure, but some specific flaws in figures and the list of references (please see notes to the authors); the author share raw data
Experimental design: This research is original, the authors define very well the research purpose which is relevant and meaningful; methods are described even though they need more details in specific points, i.e. in: Material and Methods, line 167
For Fig. 3d and Video 3, the areas of interest were selected  automatically by adjusting the threshold.

This statement is too much colloquial, Threshold of what? Which parameter was taken into account?

Otherwise, the investigation was conducted with the highest standards
Validity of the findings: Even though the image processing is quite robust and impressive by its beauty, I do have some concerns about the overall analysis of data,  for instance in

Results, line 254
We detected curved inner segments in 18 out of 21 monkey foveae. There were substantial differences in the shape of individual foveae, which corresponds to the variance among individuals observed in psychophysical measurements(He et al. 1999). The diameter of the area containing curved inner segments was 267 μm + 132 μm. The pattern formed by the outer segments was of an even higher complexity.

The authors talk about the area, but they do not deal anything on amount of cells either as an absolute number or percentage or any other ratio of curved cells compared to “regular” cells. It must be assumed that all the cells showed the reported morphology? If not, what about to perform an statistical analysis of data.

Another example is:

Results, line 263

In addition, the central foveolar cone outer segments (52 μm) were twice as long as the cone outer segments in the parafovea (26 μm).

Is there any numerical assessment for this assertion, i.e how many long outer segments out of 100 or whichever amount of cone outer segments?

Also, the conclusions are well stated, but it looks to me that in some points is too much speculative, specifically in:

Discussion, line 306
As light propagation by Müller cells through the retina (Franze et al. 2007) has been shown to be important and increases photon absorption specifically by cones (Labin et al. 2014), we hypothesize that light hitting the Müller cell plateau at an angle of 0 degrees is effectively transmitted into the photoreceptors whereas light hitting the Müller cell plateau at a different angle is partly reflected accordingly, which reduces the amount of light guided through the Müller cells. This is in accordance with the finding that retinal foveal structures reflect light entering at an angle different from 0 degrees.

On Figure 2, panel B the authors describe the Müller cells in this area as lacking organelles, Unique central foveolar Müller cells from monkeys (A) In a semi-thin section perpendicular to the optical axis the central Müller cells are translucent (arrow). (B) The Müller cells (arrow) are shown in the same orientation as in a) at high magnification. They do not contain cell organelles.
So, how could thus reflect light, when there is no refringent material inside them? Please elaborate.
Additional comments: My general comments refer on typos, mainly:

Introduction, line 67:
Stiles also showed that monochromatic light of the same wavelength
It looks redundant to me, could rephrase to “Stiles also showed that monochromatic light”.

Material and Methods, line 121
This protocol has been shown to minimize fixation artefacts.

Is there in literature reference for that statement or comes form Group experience?. Please explain it.

Figure 1
Anatomical findings in monkey foveae and cones
(A) In an electron micrograph, an extra foveal cone contains irregularly ordered stacks of photoreceptor disc membranes (black arrowheads) and spaces free of photoreceptor membranes (arrow). In contrast, the disk membranes in rods are highly ordered (white arrowhead).

There is no white arrowhead in panel (A)

Figure 2
Unique central foveolar Müller cells from monkeys (A) In a semi-thin section perpendicular to the optical axis the central Müller cells are translucent (arrow). (B) The Müller cells (arrow) are shown in the same orientation as in a) at high magnification. They do not contain cell organelles. The arrowhead marks a Henle fibre. (C) The plateau zone of a Müller cell is indicated by a white arrowhead in a section parallel to the optic axis. Henle fibers are indicated by a black arrowhead and cone nuclei by (N) (D) A 3D model shows the main part of the central Müller cells of a monkey. ( E) The central Müller cell in Fig. b (arrowheads) is shown integrated into a stack mounted from serial sections. (F) A human foveolar Müller cell 3D model is shown and its plateau zone marked by an arrow.
<!--[if !supportLineBreakNewLine]--> <!--[endif]-->

There are no panels E nor F in the figure

References, line 348
Brinkmann;A RA. Müller cells in health and disease

There are missing bibliographical data


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 ANATOMY OF THE FOVEOLA REINVESTIGATED
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: The authors did most of the suggested corrections.


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 ANATOMY OF THE FOVEOLA REINVESTIGATED
Review round: 2
Reviewer: 2

Output:
Basic reporting: I received the second version of the manuscript, which includes all the modifications according  to my first review. The manuscript is modified accordingly and my suggestiuon is tobe accepted as is
Experimental design: I received the second version of the manuscript, which includes all the modifications according  to my first review. The manuscript is modified accordingly and my suggestiuon is tobe accepted as is
Validity of the findings: I received the second version of the manuscript, which includes all the modifications according  to my first review. The manuscript is modified accordingly and my suggestiuon is tobe accepted as is
Additional comments: I received the second version of the manuscript, which includes all the modifications according  to my first review. The manuscript is modified accordingly and my suggestiuon is tobe accepted as is


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: CHARACTERIZATION OF SHIFTS OF KOALA (PHASCOLARCTOS CINEREUS) INTESTINAL MICROBIAL COMMUNITIES ASSOCIATED WITH ANTIBIOTIC TREATMENT
Review round: 1
Reviewer: 1

Output:
Basic reporting: The study is quite well written. Is the term guts the correct and more scientific term in this work. Background is good and in detail. Quoteing of literature is good.
Experimental design: Overall too many results are not well conclusive as admitted by the authors themselves. The work is very preliminary.
A main weakness of this work is for the analysis of the fecal pellets as samples. If I understand fully then the koala has many parts to its gut that do different parts of the digestion.  Is this correct. The fecal pellet is the end result. How can it be properly representative of the part of the gut where key digestion is going on. Can the authors expand their study to show at least a few koala that are analysed with different part of the gut. Or is it already know that the fecal composition is truly representative.
Validity of the findings: Some of the statements the authors make in the discussion do not seem to be correct or supported.
“Low doses of antibiotics were used here”. Is this a true wording. If it is true wording, then why was this done. Did the veterinary staff involve do this.
How would “captivity mask the effects of antibiotics”. The authors should plan to give some explanations.
The koalas were treated with different antibiotics but the authors say that the difference do not matter. They should expand on this claim.
They compare with an animals that was not treated with the antibiotics. But this was only one or perhaps two animals.  How can they do just one animal. How did they do statistics analysis with such low number.
How did the animals die. This is very important to explain. Was it due to the chlamydiae infection I guess.
Is the Lonpinellea organism known to be sensitive to the antibiotics. Could the authors test this in an actual agar plate assay. Would be very good to show confirmation.
Also is the word guts sufficiently scientific description of the koala intestine parts.
Additional comments: No additional comments