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: PROGNOSTIC VALUES OF GMPS, PR, CD40, AND P21 IN OVARIAN CANCER
Review round: 1
Reviewer: 2

Output:
Basic reporting: I have no concerns about the basic reporting of this article. It is easy to read, clear and well referenced
Experimental design: The conclusion of this study is widely exaggerated. I do not agree that you can go from Murine based model (why they didn’t use established ovarian cancer lines is not explained), compare the data to human data, identify one novel association (GMPS) and state you have a prognostic signature for OC. Post hoc ergo propter hoc it is not! This is highlighted by the fact in the discussion whereby authors outline that a human study came to a different conclusion then their work.

Prognostication should be done in the confines of already understood prognostic groups- i.e in HGS what gene are associated with better survival or in P53 mutants what passenger mutations allow for better survival. This paper doesn’t really have a hypothesis that can be actually tested. This paper asks: which mutations in(a selected –not sure how selected) MOSEC change during carcinogensis (as sequenced by ?means) and then which of these seem to have a human association in all ovarian cancers (a massive hetrogenous group) and then do any of these correlate to a survival difference (with no controlling of any confounding).

I think this paper limit it scope to simply – what are the driver mutations in MOSEC cell line? That would be within the means of this study and would make a contribution that would help with the application of this murine cancer model.

It isn’t clear how many genes/outputs were analyzed. However, if you there was more than 20 then an alpha off 0.05 is too permissive allowing associations by chance to enter into later analysis.

They refer to OC as a genetically homogenous entity – I.e. our markers prognosticate in OC … this is missing the work of the TCGA and the difference between histologies.

“Our experiments were in three biological replicates to reduce sample variations due to cell heterogeneous cultures” line 201 – so they have selected their sequenced population. Not clear how these cells were selected. Therefore, are these results generalizable to the MOSEC population, let alone human OC.

“In our current study, we found that GMPS was highly expressed in ovary cancer tissues compared with that of adjacent tissues and that GMPS expression was associated with RFS of patients”. – where did this normal tissue come from – it is not mentioned in the methods. Is this MOSEC-I vs MOSEC II?

I see nothing exciting about finding genes associated with cell proliferation are associated with cancer.

I do not see how GMPS is a better prognosticator than P53, histology, age, immunoscore etc
Validity of the findings: Apart from GMPS all the genes associated survival impact have been described in much better (human) studies.

There is no description of the NGS that was carried out. Was is exomic, genomic, intronic, panel etc

No mention of quality control, allele frequency cut offs, read depth etc

PIK3CA is associated with clear cell and endometrioid mainly – Is MOSEC associated with this histotype? I am still unclear what the MOSEC actual is a proxy of- it would seem it closely models HGS and therefore it is unusual to have a PIK3CA association
Additional comments: How does this in any way add to:
https://bcl.med.harvard.edu/wp-content/uploads/2013/10/Spentzos-et-al-2004.pdf


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: PROGNOSTIC VALUES OF GMPS, PR, CD40, AND P21 IN OVARIAN CANCER
Review round: 2
Reviewer: 1

Output:
Basic reporting: I commend the authors, this has greatly improved since the first edition. The paper now reads well and the numerous typographical errors have been corrected.

My only comment would be that in the last paragraph of the introduction basically outlines the method. I think this would be better re-phrased so that is outlined the issue the paper seeks to address. I.e what is the applicability That is:

HGS has a terrible prognosis
DEGs could help better risk stratify women with the disease so they could receive the appropriate treatment
MOSECs are a credible model of HGS
Therefore DEGS examined in the MOSECs acting as a model of carcinogenesis and applied to the TCGA for prognostic significance.
The hypothesis is that DEGs identified in MOSEC cells could help yield molecular prognostic targets and explore the biology of HGS

Also in the discussion please add a specific paragraph for strengths followed by a separate paragraph exploring the weaknesses of your study. I believe there needs to be a little bit more introspection
Experimental design: The language of this paper has now very much improved.
The methods are much clearer. Previous concerns have been answered.
Validity of the findings: Again, I think we have to be very careful about the overstatement of this work. However I believe that the authors now have got the balance right- this is interesting discovery work and the use of the TCGA adds wait to the findings in MOSEC cells.
Additional comments: This paper is greatly improved. You should be congratulated.


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: IMPACT ASSESSMENT OF HIGH SOIL CO2 ON PLANT GROWTH AND SOIL ENVIRONMENT: A GREENHOUSE STUDY
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1. Basic Reporting
English has to be revised by a native speaker, there are some edits and some sentences are difficult to read.
Some references are missing, especially in the introduction section; some suggestions are given in the ‘general comments’ section. Nevertheless, the ‘state of the art’ level of this article is acceptable.
The article is well structured ; some sub-sections are very short but this helps during reading.
The figures are relevant but they may be modified to increase readability :
-	Figure 2 : the symbols are too large, sometimes it is not possible to see the error bars ; the scaling on the Y-axis has to be detailed to allow a better reading.
-	Figure 4 : the labels a and b are not located appropriately : it is hard to understand to which curve the labels belong.
Raw data are available: it is suggested that the authors have a closer look to these data. For example, they do not consider the bivariate plot O2 vs CO2 (commonly used in soil gas monitoring dealing with CCS applications). By doing so, they may come to more in-depth description of the concentration changes during their experiment, and more specifically if some lateral heterogeneities exist. When using the data for CG container at 5 cm depth, one can find that the slopes and the correlation coefficents may differ from one sampling location to the other. This should be discussed.
Experimental design: This article meets the aims and scope of the journal. The research question is well defined, it has some interest to the scientific community dealing with CCS. Previous studies have also dealt with this subject but getting additionnal information is always useful. Nevertheless, some of the statements made in the introduction must be detailed or revised if needed. This is discussed in the ‘general comments’ section.
The ‘material and methods’ section is quite long (80 lines) compared to the discussion section (55 lines). However, some information is missing: if the equipment used during the monitoring is mentioned, there is no consideration about the accurracy nor the repeatability of the measurements. This is surprising. CO2 concentrations are only given at the percent level. This may be acceptable for high concentration range (more than 40-50% vol.), but this is not convenient for lower concentrations (O2 concentrations are given at 0.1%). The consequence is that there are no CO2 data available for NG and BG but only for CG. This has to be explained, because in studies performed in real conditions, a 1% rise of the CO2 concentration over a short time period may have some significance (e.g. link with diurnal cycle or link with CO2 intrusion). If the authors want to extrapolate their findings in the field, this has to be considered.
Validity of the findings: This article introduces new experiments to investigate the effect of high CO2 concentrations on plants. The monitoring is performed using different approaches (control plot, N2-enriched plot, CO2-enriched plot) with many monitoring points where the gas concentrations are measured regularly during one month. This is not the first time such an experiment is performed but the used geometry is appropriated and interesting results are obtained.
The authors have chosen to work with very high CO2 concentrations ; to my opinion this is one of the main debatable point in their approach. There are previous works (e.g. West et al., 2015, IJGCC 42, 357-371) that have established that a concentration of 10%-15% CO2 soil gas at 20cm depth is a threshold level for observing changes in plant coverage. Therefore one may wonder why the authors used a 40 to 60% CO2 concentration in the soil, depending on the depth the measurement is made. At such high concentration, it is known that changes will occur. It would have been interesting to work at CO2 concentrations closer to the threshold level in order to monitor the impact on plants, even if changes may have been weaker.
I would welcome a more detailed discussion on this choice of working with high CO2 concentrations.
Additional comments: Introduction section : there are several statements that must be revised.

Line 30 : leakage from a pipeline : it’s really surprising to make a first statement on pipeline leakage, because it is not the main issue when dealing of leakage possibilities and CCS. Surface infrastructure is, by nature, more easy to monitor and to instrument, and there are years of knowledge from the oil and gas industry. One of the main problem is rather the leakage trough borehole completions, old boreholes that were not well abandoned, and after leakage through faults and fractures. Moreover, I’m not sure the reference of West et al., 2011, makes a link between pipes and CO2 leakage, if you refer to this reference and the cited references.

Another statement is very surprising, in Line 32 : the authors link leakage through faults with the closure of the injection well. This is certainly a shortcut because leakage through faults may occur during storage activity or after (once the wells have been plugged), or never.

Line 34 : the references of Lewicki and Zhou are not cited appropriately : they do not correspond to leakage from faults after site closure, they correspond to near surface engineered leakages. That is fundamentally different.

Line 35 : please remember that when CO2 is injected in the soil, it does not only lower the O2 concentrations, it also lowers the N2 concentrations. This has probably no effect on plants, but this has to be mentioned to highlight that all the endmembers are taken into account.

Lines 37-38 : some references are missing : West et al., 2015, earlier mentioned. The authors may also refer to Krüger et al., 2011, IJGCC 5, 1093-1098.

Line 50 : the reference from Beaubien et al., 2008, is appropriated, but the study site (Latera) is also characterised by quite high levels of H2S ; this gas phase has also adverse effects on plants.

Line 65 : if the authors refer to some references, they may also add that the plant community is different in areas where CO2 concentrations is high in the soil.

Results section :
The CO2 gradient in the soi lis very high : the authors should add reference to other studies, to establish (or not) if such a gradient can occur naturally.
I wonder if a 0.4 pH unit difference is really meaningful – considering that pH values are often given with at ±0.1 unit (even if pH-meters can give 3 digits, this has not real significance in field applications).

Discussion :
I’ve no fundamental remark to make, because the results are in agreement with those of previous studies. Maybe the authors can comment on the discussion lines 226-230 : they discuss the presence/absence of O2 in the soil, they may also mention the role of O2 exisiting in the atmosphere.


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: IMPACT ASSESSMENT OF HIGH SOIL CO2 ON PLANT GROWTH AND SOIL ENVIRONMENT: A GREENHOUSE STUDY
Review round: 1
Reviewer: 2

Output:
Basic reporting: 1.	Basic reporting: This is a timely report into the effects of potential CO2 leakage in the soil environment from CCS storage sites. Intro and background thorough and relevant, well structured. Figs relevant and of sufficient quality. Raw data was supplied and checked. Language is generally good, with a couple of specific points (see below)
Experimental design: 2.	Experimental design is acceptable, the research question provides novel findings of biochemical and metabolic changes in response to extreme CO2 in the soil environment. Methods are described adequately for replication.
Validity of the findings: 3.	Validity of findings is acceptable with robust data. Speculation of the potential metabolic biochemistry is useful and in context and conclusions are correct for data presented.
Additional comments: Specific comments:
Line 22 – suggests that the root system affected the surrounding soil environment, but this is not dealt with in the paper. If this refers to an increase in soil pH, this is not explained in the text. Otherwise it needs re-phrasing.
Line 28 – English would be better as ‘ To ensure safe and successful CCs projects’
Line 33 – ‘ would experience a high soil CO2’
Line 73 – a conceptual diagram is proposed, not ‘will be developed’
Lines 79 and 83 – South Korea
Line 172 – soil pH was statistically significantly reduced in CG treatment
Line 197 – should read after harvest, not after injection (ambiguous)
Line 207 – after experiments had finished, not after injection
Line 208 – HWC is lower in CG and NG than BG (Table 5) – clarify/explain
Line 217 – ‘plants were influenced by high soil CO2, but not by low O2’ - NG treatment had a very high NAG content compared to BG and CG – please explain this result
Line 256 – Lake et al. 2016b
Line 257 – ‘when plant roots suffer from CO2 stress’
Line 275 – ‘reduced soil pH’
Reference list requires subscript in CO2

Table 3 second section – statistical analysis refers to data presented in Table 4, suggest moving to bottom of Table 4.
Table 5, BCG is omitted from the abbreviations footnote
Figure 3 legend should explain what a), b) and c) are.


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: IMPACT ASSESSMENT OF HIGH SOIL CO2 ON PLANT GROWTH AND SOIL ENVIRONMENT: A GREENHOUSE STUDY
Review round: 2
Reviewer: 1

Output:
Basic reporting: This is a revised version of a manuscript earlier submitted this year.
Comments and suggestions have been taken into account by the authors. The manuscript has been improved, thus it can be considered for publication.
Experimental design: OK
Validity of the findings: OK
Additional comments: OK


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: NONCONVENTIONAL OPPONENTS: A REVIEW OF MALARIA AND LEISHMANIASIS AMONG UNITED STATES ARMED FORCES
Review round: 1
Reviewer: 1

Output:
Basic reporting: Authors use the English language appropriately. Suggestions for modifying writing were minimal. The authors use several old and current references, adequate to the context of the study, but also suggest the inclusion of relevant works to complement some points of writing.

- Is the review of broad and cross-disciplinary interest and within the scope of the journal?
Yes.
- Has the field been reviewed recently?
No.
- If so, is there a good reason for this review (different point of view, accessible to a different audience, etc.)?
Yes.
- Does the Introduction adequately introduce the subject and make it clear who the audience is/what the motivation is?
Yes.
Experimental design: Article content is within the Aims and Scope of the Journal. Careful investigation with good writing. Methods need better description to replicate.

- Is the Survey Methodology consistent with a comprehensive, unbiased coverage of the subject?
More and less.
- If not, what is missing?
The authors can further detail the study methodology.
- Are sources adequately cited?
Yes.
- Quoted or paraphrased as appropriate?
Yes.
- Is the review organized logically into coherent paragraphs/subsections?
Yes.
Validity of the findings: Meaningful replication encouraged where rationale and benefit to literature is clearly stated. Conclusion are well stated, linked to original research question and limited to supporting results.

- Is there a well developed and supported argument that meets the goals set out in the Introduction?
Yes.
- Does the Conclusion identify unresolved questions / gaps / future directions?
Yes.
Additional comments: The manuscript presents a revision character and the results and conclusions contemplate the proposed objective. I make some considerations, however, to improve writing, especially some parts of the text.

- Abstract (lines 57 to 58): Visceral leishmaniasis has been extensively studied in the world, especially in endemic countries as Brazil, so I think it is pertinent for the authors to clarify that the disease is still little addressed in the US.

- Introduction (lines 84 to 86): The authors should tell when soldiers were negatively affected and cite sources consistent with the statement.

- Survey Methodology (lines 112 to 119): For this topic I make some suggestions. I believe that the authors can write in more detail what publications were considered for the review (if only original articles, common and/or systematic revisions, prior notes, brief communications, meta-analyzes, etc.). I also think it pertinent for the authors to cite the period of time considered for reading the references used (were articles sought from 1980 until today? Was a criterion of temporal selection of these studies used?). Another point that could be approached by the authors was the languages that these selected papers presented (English, Spanish, French, etc.) and the exclusion criteria of the researches that were not selected for review.

- Malaria (lines 125 to 128): The authors refer to a 2017 update that revealed 32 cases of malaria infection among US military personnel stationed overseas. How many soldiers there were among 32 cases? I find it interesting to situate the reader on this percentage of infection.

- Malaria (Causes) (lines 150 to 152): I suggest that the authors better explain this passage by highlighting that in the past, malaria was known as tertian or quartan fever, depending on the parasite species. This was related to the way in which the fever occurred in the patients after about 15 days: in the case of the tertian, the fever occurred every 48 hours (P. vivax, P. falciparum and P. ovale), and in the case of quartan, every 72 hours (P. malariae). The authors can cite references from malaria.

- Leishmania (Causes) (lines 225 to 228): In this topic I make two considerations. The authors can cite the metacyclic promastigote forms as infective for the vertebrate hosts during the blood meal of sandfly. The authors can also cite the diffuse cutaneous form as one of the clinical forms of tegumentary leishmaniasis.

- Leishmania (Causes) (lines 232 to 234): I suggest rewriting this sentence in other words. I considered the phrase confusing to my understanding.

- Leishmania (Causes) (lines 234 to 238): I suggest that the authors can cite more current US military infection data, since in the topic "Prevention and Treatment" (lines 261 to 262) the authors cite "Rowland 2015" as a reference in the passage "The reduced incidence rate of recent years has been attributed to better equipment and an emphasis on personal protective measures". What is this most current incidence rate?

- Leishmania (Symptons) (lines 241 to 242): This information is true: "Lesions can be self-resolving, as is often the case in many cases of CL", without treatment? I think that the authors can look for new references to better detail this statement.

- Leishmania (Prevention and Treatment) (lines 286): The authors refer to recent reports of treatment failures in South and Latin America leishmaniasis, but do not cite any reference to this consideration.

- Other: Military Canine Leishmaniasis (lines 312 to 314): The authors comment on a larger study volume in Mediterranean region and Brazil, however, could have cited some researches, including current studies of disease burden that have been published.

- Conclusions (line 376): The authors can remove the word “are” from italics.


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: NONCONVENTIONAL OPPONENTS: A REVIEW OF MALARIA AND LEISHMANIASIS AMONG UNITED STATES ARMED FORCES
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comments
Experimental design: As strictly a literature review, the objectives are clear but the methods were not properly described. I have missed some of the most important and recent publications in both diseases and the searching method seems to be biased to more clinical than epidemiological publications.
Validity of the findings: No comments
Additional comments: This manuscript summarizes a literature search about malaria and leishmaniasis in the US military personnel.  As strictly a literature review, the objectives are clear but the methods were not properly described. I have missed some of the most important and recent publications in both diseases and the searching method seems to be biased to more clinical than epidemiological publications. Overall, the paper is well-written and the results would be useful for future plans of improving malaria and leishmaniasis control.

Specific comments:

Line 57 - I will not use the term canine leishmaniasis since you are talking about human leishmaniasis caused by leishmania infantum, for which the main reservoir are dogs. The diseases in dogs is known as canine leishmaniasis in humans in some regions is known as zoonotic visceral leishmaniasis (ZVL) but can also be named as human visceral leishmaniasis caused by L. infantum.
Line 115 - The methodology should be more specific and include details about the searching methods. All the subject directed key words should be included. The list of words used must be limited otherwise the search will be impossible to manage. The word “etc” does not provide precise information. The methods must also include if two or three words were search at the same time and what link was used (AND/OR).
Line 161 – this reference is missing (Yohannes et al., 2016)
Line 181 - please add that has been observed in “rats”
Line 237 – Could you please add how the % of CL in British, Dutch and German soldiers compares with the % of CL in American soldiers?
Line 288 -  Please add a reference
Line 291 - None of these 2 references is about the role of dogs as the main reservoir for leishmania infantum. Please include more appropriate references
Line 291-297 - Leishmania infantum is responsible for Zoonotic Visceral Leishmaniasis in humans and rarely induced cutaneous symptoms. Some of the references used here are not appropriate, please read these 2 publications and consider to introduced them in this section  (Burza et al., 2018) (Quinnell and Courtenay, 2009)
Line 314 - Please add a reference here
Line 330 -331-  Current Leishmania vaccines in dogs have been highly questioned as a prevention strategy since don’t stop transmission and only reduce clinical symptoms. Please include some precaution to this statement.


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: NONCONVENTIONAL OPPONENTS: A REVIEW OF MALARIA AND LEISHMANIASIS AMONG UNITED STATES ARMED FORCES
Review round: 2
Reviewer: 1

Output:
Basic reporting: Is the review of broad and cross-disciplinary interest and within the scope of the journal?
Yes.

Has the field been reviewed recently? If so, is there a good reason for this review (different point of view, accessible to a different audience, etc.)?
Yes.

Does the Introduction adequately introduce the subject and make it clear who the audience is/what the motivation is?
Yes.
Experimental design: Is the Survey Methodology consistent with a comprehensive, unbiased coverage of the subject? If not, what is missing?
Yes.

Are sources adequately cited? Quoted or paraphrased as appropriate?
Yes.

Is the review organized logically into coherent paragraphs/subsections?
Yes.
Validity of the findings: Is there a well developed and supported argument that meets the goals set out in the Introduction?
Yes.

Does the Conclusion identify unresolved questions / gaps / future directions?
Yes.
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: NONCONVENTIONAL OPPONENTS: A REVIEW OF MALARIA AND LEISHMANIASIS AMONG UNITED STATES ARMED FORCES
Review round: 2
Reviewer: 2

Output:
Basic reporting: This review has improved after the revisions. Authors showed willingness to to adapt the manuscript the to the reviewers suggestion and the final outcome is an interest review   in malaria and leishmania within the USA army
Experimental design: The content is within the scope of the journal and methods are described with sufficient detail
Validity of the findings: The benefit to the literature is clearly state. Conclusions link to the original questions
Additional comments: This is a nice review that is going to be appreciated by the researches in the area of malaria and leishmania


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: INCREASED TOOTH BRUSHING FREQUENCY IS ASSOCIATED WITH REDUCED GINGIVAL POCKET BACTERIAL DIVERSITY IN PATIENTS WITH INTRACRANIAL ANEURYSMS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The sequence data was not available.
That is a road block to replicate the study.
Experimental design: The design is questionable, as the cohort is a group of rare tumor patients. How the conclusion from the cohort is generalizable is unaddressed.
The statistical methods used did not adjust for likely confounding factors, such as common demographics, prior periodontal condition, dietary and etc.
Validity of the findings: While tooth brushing is generally believed to drop diversity temporarily, it is believed to be of modest effect (Hall et al.
Inter-personal diversity and temporal dynamics of dental, tongue, and salivary microbiota in the healthy oral cavity). Since the current single time point design did not address the variability of temporal diversity change, it is hardly conclusive.

Moreover, the use of a group of rare tumor patients instead of dental patients and healthy population makes the conclusion less generalizable.
Additional comments: Given the design flaw, the article would be hardly revisable for the purpose of current conclusion. My suggestion is, the authors may find interesting points from reanalyzing their microbiome data together with the patients' tumor conditions and wrapping their data around these points.


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: INCREASED TOOTH BRUSHING FREQUENCY IS ASSOCIATED WITH REDUCED GINGIVAL POCKET BACTERIAL DIVERSITY IN PATIENTS WITH INTRACRANIAL ANEURYSMS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is written in a clear and unambiguous English.

Please make the raw data available. If possible, it would be excellent to have a self-containing script that fully reproduces the results and figures as well, together with the raw data.

Also, please properly cite all the software packages you used (e.g. QIIME, DESeq2, Trimming software, phyloseq, ...?!). Also, please refer to the used methods and statistics that are calculated (e.g. Chao1).

When it comes to the Figures, Figure 2 needs some improvements, if the abundances are merged on class level, it is not clear to me why there are more bars of the same colour? And how to interpret the parts that are black/borders? It might be worth trying out a barplot?!

In Figure 3, to me, it seems that there are more than 22 samples? Could you clarify, why there are so many dots? I suppose they should indicate the samples? If they were used also in the regression analysis, is the analysis based on the 22 samples or the ones indicated in Figure 3?

Also in Figure 4, I am not sure about the boxes of same colour, how to interpret theses. Could you please clarify this?
Experimental design: The research question is well defined. However, I have some doubts about the experimental design itself. The authors find significant differences in the gingival pocket bacterial diversity associated with the increased tooth brushing frequency but ignore the large amount of other, possible confounding factors that might need to be discussed and/or taken still into consideration, if applicable. Possible factors are

1. Is there any effect on the bacterial diversity for the time between sampling and the last time brushing the teeth? This time would be also expected to be smaller for people who brush twice a day and hence, is potentially very influential.

2. What is the effect of using mouthwash? My assumption is, people who brush more often the teeth have also the tendency to use more often mouthwash.

3. How long time before the sampling, patients ate something?

Please discuss the confounding factors as possible effects.

Also, you mentioned that the probes were taken from the deepest gingival pocket. How was this depth distributed among the three brushing groups? There certainly is an influence of periodontal probing depth on the gingival bacterial communities and hence should be similar among the groups to compare.

Further, you mention that 38 samples have been discarded from the analysis due to insufficient quality. Could you please provide a clear justification, what criteria they failed to meet and how the 22 remaining samples passed the check? Maybe add the quality checks to the supplement (maybe combined using e.g. MultiQC, if they failed on the raw data level)
Validity of the findings: The Chao1 index has (like any other Alpha diversity index) its limitations and there are sometimes large differences between Chao1 and other, popular indices. In order to declare a strong hypothesis as the authors do, I would like to see also other, commonly used indices applied to the data and see, if they support the hypothesis, also.
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: INCREASED TOOTH BRUSHING FREQUENCY IS ASSOCIATED WITH REDUCED GINGIVAL POCKET BACTERIAL DIVERSITY IN PATIENTS WITH INTRACRANIAL ANEURYSMS
Review round: 2
Reviewer: 1

Output:
Basic reporting: From the rebuttal letter, my concerns were acknowledged but mostly unaddressed. The authors did release their data, but they used a very uncommon data website and I am surprised neither NCBI or ENA was used.
Experimental design: The questioning of their design remains. The authors claim they do not want to generalize the finding but they forgot to quantify their title with the cancer types, which became very misleading if people just take the face value.
Validity of the findings: With the limited design, also remained are likely confounding factors, as also pointed out by Review #2. If the authors cannot release meta data, to reach a conclusion trustable, at least summary statistics and p-values from multivariate models should be reported, rather than pure microbiome data.
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: INCREASED TOOTH BRUSHING FREQUENCY IS ASSOCIATED WITH REDUCED GINGIVAL POCKET BACTERIAL DIVERSITY IN PATIENTS WITH INTRACRANIAL ANEURYSMS
Review round: 2
Reviewer: 2

Output:
Basic reporting: Not considered, see below.
Experimental design: After seeing the clinical information of the included samples, another issue in the experimental design became obvious. There are repeated measurements in the data, some of the included individuals have been sampled repeatedly and consequently have been included also repeatedly into the analysis.
Validity of the findings: The used methods rely on an iid assumption of the samples, which is, however, violated by including repeated measurements without taking this into account for the analysis. Please, either take the information of repeated measurements into account (=adjust the used methods accordingly), or remove the repeated measurements from the analysis.

In my opinion, using a few repeated measures biases the results tremendously and consequently the results are in their current form not valid.
Additional comments: You mention that you describe the samples now more detailed, but it was still not obvious that you were using repeated measurements in the data. As written above, either justify repeated measurements or remove them


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: INCREASED TOOTH BRUSHING FREQUENCY IS ASSOCIATED WITH REDUCED GINGIVAL POCKET BACTERIAL DIVERSITY IN PATIENTS WITH INTRACRANIAL ANEURYSMS
Review round: 3
Reviewer: 1

Output:
Basic reporting: I am still not sure about your reported sample sizes, sorry! In the abstract you write that you started with n=60 patients, but then later in the the M&M part you tell that you use 34 samples from 23 patients (out of 63 samples in total). Those numbers still do not seem to match, if you have n=60 patients in the beginning and from there then 63 samples, how can you have for 11 patients even two samples? Please, still go once more carefully over your sample size description. Also, the amount of observations (=dots) in Figure 2 does still not match the description in the M&M part. If you took in total 34 samples from 23 patients and you averaged the repeated measurements, there should be only 23 dots in that figure, if I understood it right?!! And as your regression analysis is based on this data, are you sure you applied the regression analysis on the averaged data?
Experimental design: As pointed out already in the previous review by myself and also by reviewer #1, there are conceptual problems in the experimental design as many potential confounding factors have not been controlled. Of course that is nothing that could be changed at this stage anymore, but I still miss a critical discussion of this in the manuscript. You write that you findings "are in line with these previous findings (line 159)" (e.g. that bacterial diversity increases 24h after tooth  brushing) but at the same time you have not asked the patients when they brushed their teeth last time. I believe your information of 0,1,2 brushings per day is the normal behaviour, but people might deviate from that on some days (or some brush only in the evening others in the morning).
Validity of the findings: I do not doubt that there is a correlation between the frequency of tooth brushing and the microbial diversity. The problem that I still have with this study is that you do not discuss the possible confounding factors (even after having them pointed out). Especially, in the context of missing confounding factors, please be cautious about mixing correlation and causation. (Silly example, there is a strong correlation between sleeping with leather shoes still on the feet and waking up with a headache. The conclusion would be, sleeping with leather shoes causes headache. The obvious underlying causative factor is, however, rather another one...).

That said, I think, you really should discuss still other possible effects that could cause your observation and not only bring it down to the frequency of tooth brushing.
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: THE COMPLETE CHLOROPLAST GENOMES OF THREE BETULACEAE SPECIES: IMPLICATIONS FOR MOLECULAR PHYLOGENY AND HISTORICAL BIOGEOGRAPHY
Review round: 1
Reviewer: 1

Output:
Basic reporting: Authors sequenced and analyzed the chloroplast genome of three Betulaceae species. Authors identified divergence hotspots throughout these genomes including repeats which can be used as markers for Betulaceae species.

Introduction is written in a complex way and sufficient background is not provided to understand the significance of the work. It should be rewritten with sufficient background. For example, lines 54-55, “Opinions differ, however, relating to the intergeneric relationships and genera circumscription as ranking into higher taxonomic level” is not clear what authors want to say here.

In figure 6, what is the criteria for the selecting node in phylogenetic analysis? It is not clear how the phylogenetic tree was generated? How many sequences were used and the basis of the selection ?
Experimental design: Methods should be described in detailed. All the previously described methods/computational programs should be briefly described. For example, “BEAST v2.4.8 software”, authors should explain why this software was used and what are parameters used in this software.

What is the average read length in the sequencing data? How much error rate is present in the analyzed sequences? How this error rate affected the SSRs in the analyzed data and the phylogenetic analysis?

Overall detailed description is required to understand all the parameters used in all analysis.
Validity of the findings: Conclusions are well stated.
Additional comments: Authors sequenced and analyzed the chloroplast genome of three Betulaceae species. Authors identified divergence hotspots throughout these genomes including repeats which can be used as markers for Betulaceae species. Manuscript is written well however authors need to address following issues.

1. Authors should described the parameters used in the phylogenetic analysis.

2. Figure 3 is difficult to follow. Authors can add descriptions in figure legend.

3. Figure 4 shows the variability in protein coding region or intergenic spacer regions. How this variability correlated with numbers given in Table 1?


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 COMPLETE CHLOROPLAST GENOMES OF THREE BETULACEAE SPECIES: IMPLICATIONS FOR MOLECULAR PHYLOGENY AND HISTORICAL BIOGEOGRAPHY
Review round: 1
Reviewer: 2

Output:
Basic reporting: In this work, the authors sequenced chloroplast genome of three Betulaceae species, and performed comparative genomics and phylogenetic analysis on the sequenced genomes along with some of the previously published chloroplast genomes of other Betulaceae family members to highlight genome variations, identify molecular markers, and resolve phylogenetic relationship and divergence history of Betulaceae family. The manuscript is well written, clearly explained, and there are no significant technical concerns.
Experimental design: The aims of the study are well-defined and the methods used are appropriate and sufficiently detailed. Although some clarifications are warranted as noted in general comments.
Validity of the findings: Overall, conclusions are well supported by the data.
Additional comments: 1)	While the phylogenetic trees constructed using the CPG/IGS dataset (Fig 6A and S1) differed from that constructed using PCG dataset (Fig 6B) with respect to Ostryopsis position, it is interesting to note that the topology obtained with CPG dataset (Fig S1) also differs from the topology obtained using CPG dataset in Fig 6 of Yang et al, 2018 (PMID: 30038632), wherein the Ostryopsis position in the CPG dataset topology is similar to the PCG dataset topology obtained here (Fig 6B). Can the authors comment on incongruence between the two topologies obtained using CPG datasets? Would the topology obtained using CPG dataset be different if the authors also include the other chloroplast sequences from Yang et al, 2018 (PMID: 30038632) (for example including the Ostryopsis Decaisne and/or other Corylus sequences)?
2)	On line 92-93, authors should provide the reason for selecting these 3 species in particular for chloroplast genome sequencing.
3)	On line 120, “…. were checked by aligning with homologous genes of other cp genomes…”, authors should clarify what other chloroplast genomes were used?
4)	On line 127-128, accession numbers should be provided for the chloroplast genomes of Carpinus tientaiensis, Betula nana, and Ostrya rehderiana.
5)	Authors should provide the accession number of all the chloroplast genome sequences used to construct phylogenetic tree.
6)	Some of the papers cited in the manuscript are missing from the References list. For example, Furlow 1990 on line 46, Heywood, 1993 on line 58 etc.
7)	Abbreviations are used without first defining it. For example, ITS on line 67.


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 COMPLETE CHLOROPLAST GENOMES OF THREE BETULACEAE SPECIES: IMPLICATIONS FOR MOLECULAR PHYLOGENY AND HISTORICAL BIOGEOGRAPHY
Review round: 2
Reviewer: 1

Output:
Basic reporting: Authors sequenced and analyzed the chloroplast genome of three Betulaceae species. Authors identified divergence hotspots throughout these genomes including repeats which can be used as markers for Betulaceae species. In revised manuscript, all the comments have been incorporated and manuscript has been improved.
Experimental design: In revised manuscript, authors have included details of all the experimental analysis.
Validity of the findings: Current manuscript show the detailed analysis of Betulaceae species and identified variations in genome that can be used as markers to identified the species.
Additional comments: Overall, manuscript has been improved.


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

Input:
Title: THE COMPLETE CHLOROPLAST GENOMES OF THREE BETULACEAE SPECIES: IMPLICATIONS FOR MOLECULAR PHYLOGENY AND HISTORICAL BIOGEOGRAPHY
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Authors have addressed all my concerns and manuscript is now suitable for publication.


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

Input:
Title: FOOD-BURYING BEHAVIOR IN RED IMPORTED FIRE ANTS (HYMENOPTERA: FORMICIDAE)
Review round: 1
Reviewer: 1

Output:
Basic reporting: - Good English for most of the article, except some sentences that need to be reworked.
- Interesting observations are reported, but the paper lacks good framing that would increase its impact. Since we can assume that most food that ants encounter would quickly go bad (e.g. insects), what may be the fitness benefits of burying food in the case of ants?
- Classic manuscript structure.
- Good figures.
- Raw data are supplied.
- Sometimes, interpretation of results in light of wider literature (e.g. ‘reserve ants’, psychology of superorganism) requires more explanation.
Experimental design: - Research is original and within the scope of the journal.
- The experimental design is simple and efficient. However, I have a problem with the control that was used (i.e. piece of plastic that resembles the sausage). The authors state in the introduction that ants are known to use soil particles to collect and transport liquids back to the nest, or to break the water tension. If the food burying behavior evolved as a way for ants to keep excess food as a reserve, and not as a response to physical property (e.g. moisture), a control that has a similar moisture/consistency to sausage but no nutritional properties (e.g. plain agarose gel) would be an appropriate additional control. At best, I’d recommend re-running a control experiment with a different control. But I am aware that this may not be possible, so the authors should at least discuss this issue to make this limitation obvious to the reader.
- I am unsure about some of the statistical methods. For instance, in Figs. 4b and 5a (and tables S2 and S3), the authors seem to be running multiple ANOVAs on non-independent measurements (i.e. time series). Colony was added as a random effect, which is good, but will not compensate for non-independence of measurements across time points. Repeated measure ANOVA may be more appropriate? Please investigate.
- Methods are otherwise clear and well described.
Validity of the findings: - The control I deemed not appropriate limits the scope of possible conclusions of the study, but the author’s conclusions are appropriately not overstated in that regard. There are a lot of speculations to be made in why the ants would have evolved such behavior, and the authors could expand their discussion a bit by adding more details (and make clear that these are speculations). For instance, the authors touch on the idea of collective-level cognition through a behavioral analogy with mammals, which could be perceived as slightly extravagant in this case unless they further detail their thought process. Similarly, the parallel with so-called ‘reserve ants’ is not immediately obvious, and needs more explanation.
Additional comments: The authors describe a simple experiment that aims at studying food-burying behavior in Fire ants, and provide detailed measurements about this phenomenon. However, the article would benefit from better framing, and while the methods and result sections are flowing nicely, more work needs to be done on the structure of the introduction and discussion.
Experimental design could be improved, as in the current state the scope of the conclusions are limited. However, I think the authors could choose to acknowledge the limitations associated with the experimental design (e.g. inappropriate control) without having to re-run experiments as the article contains interesting observations.


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: FOOD-BURYING BEHAVIOR IN RED IMPORTED FIRE ANTS (HYMENOPTERA: FORMICIDAE)
Review round: 1
Reviewer: 2

Output:
Basic reporting: The Authors focus on an interesting foraging behavior observed in the red imported fire ant Solenopsis invicta, and never described (in these terms) in other ant species.
The article structure generally conforms to PeerJ standards. However, folllowing the “Instructions for Authors” provided by PeerJ, I suggest to add a “Conclusions” section to underline the most relevant results argued in the “Discussion”. All the figures are well thought, extensively described and useful to support the comprehension of the text. As required by PeerJ policy, raw data are completely provided, well organized and the association raw data/statistical test/figure is clear. Moreover, supplemental tables supply statistical results that have no place in the main text. Relevant results to tested hypotheses are all reported.
In the “Introduction”section, references provided by the authors are adequate to supply information on this topic. However, there are some critical issues to consider:
-	Several times, the Authors mention observations referred to as unpublished data. Only in one case, I suggest to delete the entire part of the sentence with the reference (Line 64-65: “Carebara diversa…”).  In the other cases, the Authors’ preliminary observations on burying and foraging behaviors of Solenopsis invicta may be organized in a separate paragraph of the “Materials and Methods” section and more details may be provided (see, for instance, L 78-79, L 110-111, and L 113-114)
-	L 91-93: the sentence lacks a reference. I suggest adding the reference or deleting the sentence
-	L 95-96: the Authors refer to “videos” never mentioned before. I suggest rephrasing the sentence.
In my opinion, the language is rather clear and technically appropriate along the MS. Nevertheless, I advise the Authors to carefully review the text to correct many typos. See, for instance,
-	Line 25: transport were suppressed
-	Line 27: starved conditions
-	Line 70: when the food are not needed
-	Line 78: the burying and foraging behaviors seems
-	Line 262: when ants are hunger
-	Line 268: further studies are need
Experimental design: The present paper fulfills the aims of the journal. There are two main research questions that are defined in details and relevant to fill a lack of knowledge on this topic. Materials and methods used to conduct the experiments are very well described and easy to understand. Just a few concerns:
-	Line 131: the Authors introduce the use of “false food” without explaining why. I think false food is used as a control to test if an object (not food) can, somehow, elicit S. invicta foraging/burying behaviors, but this has to be made explicit. In addition, the choice of the material used to create false food needs an explanation, too.
-	Lines 167 and 171: second and third tests are run as one-way ANOVA, not as two-way ANOVA. In fact, as the Authors write, the fixed factor is only one, that is location (L 168) and behavioral pattern (L 172), respectively. The same mistake is repeated in Figure 4 and 5 Legends (L 469 and L 475) and in the supplemental material (Table S2 and S3).
-	Line 173: defining worker size class, three categories are mentioned (small, medium and large), but no measures for each category are provided.
-	Line 175: point (iii) is not clear. I think there is a mistake in the expression “number of relocated particle time for each ant” and suggest deleting “time”.
Validity of the findings: The “Results”section follows the same organization of the “Methods”, resulting very clear and complete. Statistical tests are appropriate and all the results provided fulfill the aims of the work. Also the “Discussion” section is well organized and strong results are widely discussed. Only few points to review:
-	At the end of the discussion (L 304-306), the Authors give suggestions on the use of baits in areas infested by S. invicta. In my opinion, this part needs some more sentences to allow the reader to return on this issue mentioned above in the introduction.
-	Figure 5c is not mentioned in the main text. I suggest including this reference at the end of line 232.
-      Figure 5 Legend (L 481): delete “were” in “each particle were by each ant”.
Additional comments: In the “Key words” section, the word “particle” is included. I think “particle” is a too general term and can be confounding. I therefore suggest substituting it with “soil particle”.


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: EFFECTS OF DIFFERENT TRAINING MODALITIES ON PHOSPHATE HOMEOSTASIS AND LOCAL VITAMIN D METABOLISM IN RAT BONE
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors described the effects of different training modalities on phosphate homeostasis in a rat model. They analysed four experimental groups: control rats; rats subjected to peak power (PT); animals subjected to endurance training (ET) and a group of rats subjected to a peak power followed by an endurance training (PET).
The paper could be interesting but there are many issues that should be clarified. Moreover, some typing error should be checked (for example line 96 and 337).
Experimental design: The experimental design is well described. However since FGF23 is a phosphaturic hormone, the measurement of phosphate in urine should be assessed. Moreover, in order to assess phosphate homeostasis and its correlation with PTH and FGF23, serum vitamin D levels should be measured.
Validity of the findings: The paper lacks of significant relevance since no differences were revealed between training-subjected rats and controls, except for PTH serum levels.
Additional comments: The authors submitted the paper entitled: “Effects of different training modalities on phosphate homeostasis and local vitamin D metabolism in rat bone”. Their experimental design is well described and the research question is meaningful. However some issue should be clarified as reported in previous sections.


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: EFFECTS OF DIFFERENT TRAINING MODALITIES ON PHOSPHATE HOMEOSTASIS AND LOCAL VITAMIN D METABOLISM IN RAT BONE
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors showed that neither FGF23 mRNA and protein expression levels in cortical bone nor FGF23 plasma concentrations differed between the groups. Additionally, they demonstrated that the mRNA expression levels of SOST, DMP1, PHEX and MEPE were lower after PT in comparison to ET and PET. Moreover, expression levels of CYP27b1 and VDR were also decreased after PT compared to ET. Author observed no differences in mRNA expression of CYO27b1, CYP24, VDR, NaPi-IIa and Na-Pi-IIc contransporters. The authors analyze serum levels of FGF-23, PTH, calcium and phosphate concentrations, but only serum PTH concentrations were higher after PT in comparison to controls.
1. In the ‘Introduction’ section line 97-100 – the authors should describe more precisely and widely the effects of different types of training on systemic vitamin D and local FGF23 expression.
2. Discussion - last paragraph: The authors note their key finding that the high intensity peak training may possible have caused changes in local phosphate regulation and vitamin D signaling within bone compared to endurance training.  However, this finding deserves a bit more comment about the potential effects and mechanisms of local mechano-response in bone on systemic component.
Experimental design: 1. The dietary intake of calcium phosophate and vitamin D were not described.

2. The authors should also measure the concentration of 1,25-di-hydroxyvitamin D3 [1,25(OH)2D3] in the serum of rats.

3.  In the ‘Materials and methods’ section: Immunochemistry and Tissue preparation and mRNA extraction,  the authors should precise which parts of the right tibiae (it was a proximal/ distal  part of tibia?, it was the same region in each rat?) were taken under the investigation.

4. The number of animals is too small.

5. Authors should comment on the associations between examined parametres, if they are.
Validity of the findings: no comments
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: EFFECTS OF DIFFERENT TRAINING MODALITIES ON PHOSPHATE HOMEOSTASIS AND LOCAL VITAMIN D METABOLISM IN RAT BONE
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors described the effects of different training modalities on phosphate homeostasis in a rat model. They analysed four experimental groups: control rats; rats subjected to peak power (PT); animals subjected to endurance training (ET) and a group of rats subjected to a peak power followed by an endurance training (PET).
In the reviewed paper many issues have been clarified and typos have be checked.
Experimental design: The experimental design is well described. The authors added data that lacked in the previous version, for example serum vitamin D levels measurement, as suggested. Moreover they explained why phosphate in urine could not be evaluated.
Validity of the findings: In the reviewed version of the paper conclusion are limited to supporting results. Moreover the authors provided alternative explanations for inconclusive results and discrepancies, thus most of issues not well clarified in the previous version have been specified.
Additional comments: In the paper entitled: “Effects of different training modalities on phosphate homeostasis and local vitamin D metabolism in rat bone" experimental design is well described and the research question is meaningful. In the reviewed version the most of the issues has been clarified and discrepancies and limitations of the study have been specified.


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: EFFECTS OF DIFFERENT TRAINING MODALITIES ON PHOSPHATE HOMEOSTASIS AND LOCAL VITAMIN D METABOLISM IN RAT BONE
Review round: 2
Reviewer: 2

Output:
Basic reporting: In general, the authors did a good job of addressing the original review. However, the Authors should prepare the improved manuscript properly. In this file the Reviewer should  receive clear text without deletions of the text, it impedes reading of the manuscript. All changes implemented in the text sholud be marked in red colour.
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: GPS’ MOTIVATION FOR TEACHING MEDICAL STUDENTS IN A RURAL AREA—DEVELOPMENT OF THE MOTIVATION FOR MEDICAL EDUCATION QUESTIONNAIRE (MOME-Q)
Review round: 1
Reviewer: 1

Output:
Basic reporting: Generally well written but there are a number of grammatical errors (eg ln 82 has/have), spelling errors (eg ln 82 retierement), poor word choice (ln 58 “shortness” rather than “shortage”) and problems with punctuation (eg ln 254 quote marks). Introduction and background are relevant. Table layout could be improved eg for Table 1: include “n” (with % in brackets); is it necessary to include both %Yes and %No when total are always 100%? Suggest that Tables 4, 5, 6 and 7 are combined into a single table.
Experimental design: Experimental design is adequate and well described. Include “n” for number of GPs invited to take part (ln 118), and number that attended informative meeting (ln 131). Normal terminology is “slightly agree” and “slightly not agree” instead of “rather agree” and “rather not agree”.
Validity of the findings: I do not have the expertise to comment on the appropriateness of the statistical tests chosen. The questionnaire that has been developed addresses a clearly identified need, and appears to yield valid results.
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: GPS’ MOTIVATION FOR TEACHING MEDICAL STUDENTS IN A RURAL AREA—DEVELOPMENT OF THE MOTIVATION FOR MEDICAL EDUCATION QUESTIONNAIRE (MOME-Q)
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is written in a clear language with few minor weaknesses (see below) but should be improved in details. In introduction, statements should be proved with (current literature) references consequently.
-----
- Please add absolute numbers where % is stated.

- Line 61: sentence "Furthermore….) is hard to understand. Please rewrite with less commas.
-Line 55/59: reference missing
- Line 64.66: please correct: three months in ambulant care (not only General practice).
- please check spelling in references (line 581, capital letters)

- please check tables and add legends
- in table 1 age is missing. Please add absolute numbers and missing values
- in table 1: practice size can not be correlated with single/group. Please change into "practice form"
- table 1: please add information about the difference practice assitant/practice nurse
- please add the questionnaire as a table, or define the items in table 2. These Information is crucial and should not be reserved to supplements.
- table 2: is this right with 28 items? why not 24?
Experimental design: The research question (line 111-114)  should be focussed and adapted to the abstract (construct and test a questionnaire) and the title. Which is the main question -  "to develop a questionnaire" (abstract, title)  or "to figure out motivation) (line 111) -??

The rationale should then focus more on the research question. Information on known motivational factors for teaching for physiscians and General Practitioners should be added, with literature references. In Line 99-104 I miss the context, and expect factors on teaching motivation and why a questionnaire for GPs is needed in addition to the existing instruments (add further information after line 105, maybe from the discussion line 442 ff)

Some other information shows less context to the research question (line 84-86, 92-96) and is expendable.

The Methods section needs more details, and more focus on the research question. Please check the whole section for any potential relevant information, i.e.:
- line 117: From which source did you get the contacts? Were all GPs invited, or all practices?
- line 120: what is meant by work perspective?
- line 131: how many took part?
- line 149-153: please explain further, please cite which literature is meant
- missing data: how did you handle missing data?

Further Instruments: What is the context of this  questionnaires ? Are they important for the development of the questionnaire?

Development of questionnaires:
-Please provide information on the items: which items derived from the literature and from the discussion rounds?
- Please provide more information why you added qualification of non medical staff.

Results:
- Line 211: Please start with numbers of GPs invited and number of participants
- please show data on "missing data"

Discussion:
-please re-write the first paragraph  stating the relevant results corresponding to the research question.
-Please add findings from the literature on your statements line 397-402. Are these results known before?
- In total, the discussion should focus more on relevant findings regarding the research questions (based on existing literature) .
- line 404 following: please be more careful with the interpretation, in particular since data are based on motivation. I miss the reflection of the a gap between motivation, participation in training programs and educating students in reality.

- line 415 ff: the context to the research question is not fully clear. If staff education might play a role, please explain before why you take this into consideration, and how staff education works in Germany. In the discussion section please stay focused - is line 417 -422 really important, and why?

 limitations:
- development of the questionnaire is based on a GP population in a rural area with shortness of physicians. For further research, the questionnaire should be validated with a population of urban GPs. Are there any known results from other authors?
Validity of the findings: Novelty is assessed in line 456 -  since PeerJ explicitely wants  to avoid statements on impact and novelty, this seems expendable.

Please limit the conclusions to research questions and results, and avoid speculative statements (line 466, be careful of the motivation - reality-gap)
Additional comments: With developing a motivation questionnaire for General Practitioners, you treat a relevant theme on a solide methodological base, and present  results in a clearly written manuscript.
However, quite a number of more or less major/minor neglects (see above) impair the scientific presentation substantially.
Please revise the whole manuscript intensively. Beyond the quoted examples, rationales and details (references, numbers) should be supplemented, and the whole text and all tables should be checked carefully regarding completeness and comprehensibility.


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: GPS’ MOTIVATION FOR TEACHING MEDICAL STUDENTS IN A RURAL AREA—DEVELOPMENT OF THE MOTIVATION FOR MEDICAL EDUCATION QUESTIONNAIRE (MOME-Q)
Review round: 1
Reviewer: 3

Output:
Basic reporting: Good literature review and description of findings apart from abstract. Results and conclusion section needs re-writing. E.g., authors mention "Correlations with the MBI were in the expected directions" without providing any detail in results section and then mention factors in the conclusion which were not mentioned in results.
It is suggested to highlight the salient takeaway from the study in the abstract and conclusion be based on the described results in the abstract.
Experimental design: Research question is well defined, relevant and meaningful and within the scope of journal. Methods have been described in detail. However, readers would want to know more about the factors affecting motivation so as to see if anything can be done to enhance this. Detailed analysis with discussion of the factors need to be added so that research can help in improving the motivation levels in the long term.
Validity of the findings: Conclusions of the article are well stated and supported by data, however, same is not true of the abstract conclusion which would need to be improved as stated above.
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: GPS’ MOTIVATION FOR TEACHING MEDICAL STUDENTS IN A RURAL AREA—DEVELOPMENT OF THE MOTIVATION FOR MEDICAL EDUCATION QUESTIONNAIRE (MOME-Q)
Review round: 2
Reviewer: 1

Output:
Basic reporting: The manuscript improved, still, please add absolute numbers in the abstract (results).
Experimental design: The manuscript improved, in particular, the research question is more focused now and relvant information has been added.
Validity of the findings: The manuscript improved.
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: GPS’ MOTIVATION FOR TEACHING MEDICAL STUDENTS IN A RURAL AREA—DEVELOPMENT OF THE MOTIVATION FOR MEDICAL EDUCATION QUESTIONNAIRE (MOME-Q)
Review round: 2
Reviewer: 2

Output:
Basic reporting: Authors have made the necessary changes and manuscript is suitable for publication now.
Experimental design: Authors have made the necessary changes and manuscript is suitable for publication now.
Validity of the findings: Authors have made the necessary changes and manuscript is suitable for publication now.
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: ACCESSIBLE MOLECULAR PHYLOGENOMICS AT NO COST: OBTAINING 14 NEW MITOGENOMES FOR THE ANT SUBFAMILY PSEUDOMYRMECINAE FROM PUBLIC DATA
Review round: 1
Reviewer: 1

Output:
Basic reporting: ENGLISH: English is clear, at least for another native portuguese speaker. However, I could identify some typos throughout the MS. For example, 1 - on the fourth line of the Abstract authors write "... amount of genome data ..." rather than "amount of genomic data"; 2 - at the end of the Abstract "Formcidae" [missing i] rather than "Formicidae"; 3 - 1 to 9 are frequently written as numerals; 4 - also pay attention to prepositions and conjunctions, as in line 188 where authors used "... the coverage was higher once the entire ..." and it should be "higher as the entire".

ARTICLE STRUCTURE: In Figure 1 Cytochrome oxide I and II are referred as COI and COII in the caption but as cox1 and cox2 in the figure. Should be harmonised. The caption of Figure 2 states “Synteny of all complete mitogenomes available on Genbank”, but only five mitogenomes are shown. From the main text, it is easy to infer those five mitogenomes are representative from those available in Genbank for the family, but caption should be more precisely written. Also the caption of Figure 2 says “arrow(s)”, but there are lines and not arrows in the figure.
Experimental design: METHODS:  Line 128 – Authors say “… except by the dataset for Tetraponera rufonigra, that had to be trimmed […] to produce sequences with the same length”. This is not totally clear. The dataset for the other species were not trimmed? Maybe a little more background on the used datasets would be elucidative. Moreover, should not the datasets for all species be trimmed for their quality (to guarantee, for example, PHRED > 30)?
Validity of the findings: Line 261 - "P. ferrugineus group have approximately the same genome size in bp, suggesting that this group is monophyletic.”. Genome size per se is not suggestive of phylogenetic proximity or relationship.
Line 290 – “(iii) our own observations regarding mitogenome size.”. Same comment as above.
Line 365 – “In the later case [tree using the complete mitochondrial sequence], a clade consisting of myrmicine ants Myrmica scabrinois, Pristomyrmex punctatus and Atta texana appear as basal group”. However, these three species does not form an clade in the correspondent figure, as they do not share an exclusive common ancestor.
Additional comments: The MS #32218 reanalyses raw reads from high throughput DNA sequencing deposited in public databases to make more sense from this freely available information, to increase the amount of structured genetic information about an ant family and to contribute to the understanding of their evolution and ecological habits. In the opinion of this reviewer it was performed in accordance with the standard methods used in the field, it has merit and, therefore, should be accepted for publication. Before final acceptance, however, the points commented in the first three sections should be addressed. In addition, I also suggest: 1 - line 80, include "ecological" in "There are two known groups ..."; 2 - Line 252, "... AT bias in the control region that exceeds 90%", authors could provide the percentage of AT in the control regions of the newly assembled mitogenomes; and 3 - in the discussion, authors should consider to give more emphasis to the "comparative mitogenomics" rather than to the "Phylogenomic relationship of Formicidae inferred using mitogenome data". Note that the "comparative mitogenomics" covers half of a page while the "Phylogenomic relationship of Formicidae inferred using mitogenome data" spams more than five pages. The main contribution of this paper is the "Assembling 14 new mitogenomes", as reflected in the title, but not in the discussion.


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: ACCESSIBLE MOLECULAR PHYLOGENOMICS AT NO COST: OBTAINING 14 NEW MITOGENOMES FOR THE ANT SUBFAMILY PSEUDOMYRMECINAE FROM PUBLIC DATA
Review round: 1
Reviewer: 2

Output:
Basic reporting: All information are in the pdf that I attached.
Experimental design: All information are in the pdf that I attached.
Validity of the findings: All information are in the pdf that I attached.
Additional comments: All information are in the pdf that I attached.


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: PRIORITIZING BONA FIDE BACTERIAL SMALL RNAS WITH MACHINE LEARNING CLASSIFIERS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript describes an exploration of machine learning, specifically classification, methods to predict novel small non-coding RNAs (sRNAs). Using seven features defined for sRNAs and several well-established classification algorithms, the authors rigorously evaluated how well these algorithms perform for sRNA prediction. An encouraging aspect of this evaluation is that training and validation examples, albeit small in number, are drawn from multiple bacterial species, including a validation set from a species not in the same taxa. The results show that Random Forest (RF) is the best performing algorithm overall, with different features contributing to various levels in this performance.

The most general weakness of the manuscript is the lack of biological justification/explanation of several aspects of the study on an otherwise biologically important problem, such as the following:
•	A justification of why these seven features were selected and not others.
•	An explanation of the observed importance of the features in the RF model (Fig 6) beyond the data availability arguments presented in the Discussion.
•	The significance of validation sets from the same and different taxa isn’t discussed until page 11 (lines 322-3). Even here, it’s unclear why the results for Ec are worse than those for Mt given the above differences in taxa.
These and other biological aspects of the study need to be better explained/justified.

The manuscript is generally well-written, except for minor errors like sevens (should be “seven”) and exploited (use a more positive word) in the abstract itself. Also, the term “data” should be treated as plural everywhere, not singular (e.g. data are/were, not is/was). The manuscript will do well with another round of close proof-reading.
Experimental design: The weakest aspect of the study is the small size of the training and validation sets (Table 2) the conclusions are based on. While it is understandable that it is difficult to get reliable data for a relatively novel problem like this, appropriate precautions like the following should be followed when reporting results:
•	Given that the training and validation sets are already small and randomly determined to begin with (Table 2), it is imperative to create multiple such training and validation sets and all reported results must be shown as averages along with error bars, e.g., in Figure 2. From the first paragraph of the Performance Assessment section, it appears that an effort is made in this direction, but not clearly stated, and is not adequately reflected in the results, which is a must.
•	As noted by the authors themselves, AUC is not an appropriate evaluation measure for the unbalanced training and validation sets employed in the study. Still, AUC is used as the main evaluation measure (Fig 2), as well as the measure optimized in various classification models. The same processes should be conducted using the precision-recall-Fmeasure measures, which are much more appropriate for such situations, and the consistency of the results should be rigorously examined. Refer to the following articles for details:

Lever, J., Krzywinski, M. & Altman, N. Points of Significance: Classification Evaluation. Nature methods 13, 603–604 (2016).

Saito, T. & Rehmsmeier, M. The precision-recall plot is more informative than the ROC plot when evaluating binary classifiers on imbalanced datasets. PLoS One 10, e0118432, https://doi.org/10.1371/journal.pone.0118432 (2015).

•	The training sets are arbitrarily designed to have 3 times the number of negative examples as compared to the positive ones. Sensitivity analyses should be conducted to assess the dependence of the results on this ratio.
•	The authors have taken the appropriate step of testing the statistical significance of classifier performance differences. However, the Friedman-Nemenyi tests are recommended to be more appropriate for this testing in Section 3.2 of this paper: Demsar, J. Statistical Comparisons of Classifiers over Multiple Data Sets. J. Mach. Learn. Res. 7, 1–30 (2006). The Critical Difference (CD) plots discussed in this paper are also a better way to visualize the results of such tests than Table 2 of the manuscript. It’ll be useful to test the validity of the current results based on the Friedman-Nemenyi tests and visualize the results as CD plots.
•	Finally, the purpose of violin plots in Figure 3 is unclear and not adequately explained. Better visualization(s) and/or explanation(s) should be used in the next version.
Validity of the findings: The findings are generally valid, but must be strengthened based on the points raised above.
Additional comments: Addressing the above comments should strengthen the manuscript and make it more acceptable for publication.


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

Input:
Title: PRIORITIZING BONA FIDE BACTERIAL SMALL RNAS WITH MACHINE LEARNING CLASSIFIERS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall, the manuscript was well written. I did notice a few typographical errors.

The Introduction was relatively short. It would be helpful if the authors provided additional context on identifying bacterial sRNAs, in general. What research applications exist after these have been identified? Have any other researchers developed bioinformatic algorithms for prioritizing these? If so, what techniques did they use and how do those differ from your own? Also, why were these specific sequence properties selected for the machine-learning analysis?

I appreciate that the authors provided source code and have made it easy for others to execute their software! I am not sure I understand why the provided software for ranking sRNAs is in the R language whereas their analysis was performed in Python. The outputs should be similar, but it would help to at least provide an explanation about this, if not redo the analysis in the paper using R.

Along those lines, the authors should provide the specific code (and raw data) that they used in their analyses.

Figure 2 conveys the message that AUC values differed depending on the species and that LR performs relatively poorly. But the large number of bars makes it difficult to discern these conclusions (and perhaps others that could be discerned). Perhaps using violin plots like Figure 3 would be better than bar plots.
Experimental design: I am unsure about the way that the negative instances were generated. In my understanding, the authors shuffled sequences from the positive instances. Are these sequences different enough from what you would see in a "real" genome that it would be easy for an algorithm to distinguish between the positive and negative sequences? Wouldn't these negative sequences have the same properties as the positive sequences, at least for some of these properties (distance to the closest predicted promoter site, distances to ORFs, etc.)? Or was genomic position somehow randomized so that these would differ? Not enough details are provided to judge whether this was performed in a reasonable way.

The dataset has a 3:1 ratio of positive to negative instances. Why was this ratio selected? Might a more (or less) extreme ratio better represent reality?

The authors state that they performed "five training runs" for each combination of classification algorithm and data set. Previously, they state that the training sets had 80% of the total data. In what way did each of these training runs differ from each other? Did they use different subsets of the original training sets? Or were they different 80/20 splits of the full data set? If it is the latter, then this could significantly bias the results. In addition, the manuscript states that "The five training runs were done after optimizing the classifiers' parameters with LOOCV." Please be more clear in describing what data were used for this optimization.

Why were no E. coli or M. tuberculosis data used in the training sets? I'm not saying it should, but I didn't see any justification for this stated in the manuscript.

On line 87, it says that a range of [-150, length of the sequence] was used. But if there was no promoter in that region, then a value of -1000 was used. Perhaps I am misunderstanding, but why not just use a value of -1000 from the start, as is indicated on line 89?

I am unsure why the authors used sklearn for all the algorithms except Multilayer Perceptron. sklearn has an implementation of Multilayer Perceptron.

Did the authors generate probabilistic predictions? Or binary predictions?
Validity of the findings: I am unclear on why the authors used the metrics that they did to evaluate algorithm performance. They state that the AUC is susceptible to imbalanced data. Although that may be true in some extreme cases, it is much better than most other metrics for imbalanced data. The authors also use a few combinations of precision and recall. They evaluated prediction using recall rates of 10%, 40%, and 60%. It seems that 90% should also be used to make this symmetrical, but the authors did not state anything about this. Furthermore, why not use AUPRC instead of of using these arbitrary thresholds?

The Discussion and Conclusion were fine, but I'd have to have answers to some of my previous questions to fully evaluate the validity of these statements.
Additional comments: The authors have used machine-learning to predict whether small bacterial RNAs are putative based on properties of DNA sequences. This is a clever approach because they rely not on the specific sequence but rather on metadata about the sequences, thus potentially providing better generalizability.


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: PRIORITIZING BONA FIDE BACTERIAL SMALL RNAS WITH MACHINE LEARNING CLASSIFIERS
Review round: 1
Reviewer: 3

Output:
Basic reporting: References:  The Random Forests method was proposed by Breiman.  The other references provided for the method are not the random forests method.  In the context of the low dimensional data used by the authors it probably doesn't matter though, since they use all features in every tree.
Experimental design: No comment
Validity of the findings: 1.  Identification of sRNAs is an active area of research, and many methods for this task have been proposed.  There is no comparison of the authors' results with any other published method, so it is not possible to assess their contribution.

2.  The authors use a few easy to compute features.  Existing methods use a wealth of other information, including comparison to related bacteria, base composition information.  Several methods predict sRNAs and their targets at the same time to obtain increased accuracy.  See e.g.
Pichon, Christophe, and Brice Felden. "Small RNA gene identification and mRNA target predictions in bacteria." Bioinformatics 24.24 (2008): 2807-2813.

3.  The accuracy of the method is likely not sufficient to be useful for applying the method on a genome-wide scale, where even a small false positive rate can lead to many erroneous predictions.

4.  It's not clear how the negative examples are generated - the authors state that their sequences are shuffled versions of the original sequences, but it's not clear how the location is chosen, since that has an effect on the other features.  Simply shuffling is potentially producing "easy" negative examples, since those are sequences that do not necessarily have the characteristics of real genomic sequences.  Random sequences from the genome are likely a better choice; some of them might be sRNAs, but the contamination level is likely quite small, and would not present an issue.

5.  Generating p-values for comparing classifiers is a tricky proposition.  See:
Salzberg, Steven L. "On comparing classifiers: Pitfalls to avoid and a recommended approach." Data mining and knowledge discovery 1.3 (1997): 317-328.
Additional comments: Another minor comment:
Scientific notation:  2e-16 is 2*10^(-16) and not 2*e^(-16)!


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

Input:
Title: PRIORITIZING BONA FIDE BACTERIAL SMALL RNAS WITH MACHINE LEARNING CLASSIFIERS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have made a substantial effort to address the reviewers’ comments, but several issues still remain:

1.	The reasoning for the selection of the features on lines 68-71 should be supported by data and/or references.
2.	The authors state that the recall rate of promoter prediction programs isn’t very high. So, what is the impact of this on the sRNA prediction results? Similar issues exist presumably for the other feature extractors as well. What is the impact of those?
3.	All the statements added in lines 370-390 to explain the observed importance of the features in the RF model must be supported by data and/or references.
4.	The fonts in Figure 4 are too small to be readable.
5.	The term “FDR corrected pvalue” is redundant – FDR is corrected pvalue, but it should also be mentioned how the FDR is obtained.
6.	The forward slashes in Figure 8 is an atypical way of showing the variation. Why not show a curve, or a region, whatever is appropriate?
Experimental design: 1.	The reasoning for only creating a 1:3 unbalanced dataset isn’t satisfactory, especially because this factor is expected to have a major impact on the prediction performance. So, this ratio has to be varied to measure this impact.
Validity of the findings: 1.	As stated on line 361, “sRNARanking’s specificity of 88% is comparable to the 91% specificity of Barman et  al’s approach at a sensitivity of 85%.”. So, what is the benefit of this study compared to Barman’s?
2.	Why isn't LR included in the CD plot in Figure 6? Also, unless there is a novel interpretation of the CD plot (the order seems to be reversed), RF seems like the worst performer instead of the best, i.e., is the rightmost entry instead of the expected leftmost.
3.	The utility of the violin plot in Figure 3 is still unclear. Typically, when such a plot is shown, there is a variable on the Y-axis, e.g. individual genes’ expression, and the plots show the dependence of this value on the factors listed on the X-axis. So what is the parallel interpretation here? Are the authors calculating a per-example AUPRC? This has to be explained clearly when Figure 3 is mentioned on line 309.
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: PRIORITIZING BONA FIDE BACTERIAL SMALL RNAS WITH MACHINE LEARNING CLASSIFIERS
Review round: 2
Reviewer: 2

Output:
Basic reporting: I have no additional comments.
Experimental design: I have no additional comments.
Validity of the findings: I have no additional comments.
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: PRIORITIZING BONA FIDE BACTERIAL SMALL RNAS WITH MACHINE LEARNING CLASSIFIERS
Review round: 2
Reviewer: 3

Output:
Basic reporting: The authors have addressed most of the concerns raised in my initial review.  The comparison with existing methods improved the manuscript significantly.  However, several comments remain.
Experimental design: - The authors added a comparison with other published methods.  Although the same positive examples were used, it's not clear if the method for choosing negative examples, and their numbers were the same.

- I agree with reviewer Pandey remark about the evaluation procedure employed by the authors, and have additional comments in that regard.  In machine learning the term "validation set" refers to data that is used for choosing classifier hyperparameters.  The authors appear to use this term to describe the test set on which performance is evaluated.  Furthermore, the fact that the authors mention specific hyperparameter values as optimal when discussing the various classifiers is inconsistent with the mention that multiple training sets were used, as each choice of training set might end up with different optimal hyperparameters.
The model selection/evaluation proposed by the reviewer Pandey makes a lot more sense than the one used by the authors in view of the small number of examples.  Measuring the variability of the performance over several training runs has limited usefulness, and in algorithms such as logistic regression which has a single global optimal solution that is even more the case.  Finally, using LOO cross validation for parameter selection is clearly overkill.  Nested cross-validation is the standard technique for classifier evaluation and model selection in the area of machine learning, and is well supported by packages such as scikit-learn.  The following paper is a good reference on this topic, and goes even further, suggesting repeated nested cross validation as a good approach for small datasets:
https://jcheminf.biomedcentral.com/articles/10.1186/1758-2946-6-10
Validity of the findings: - In my initial review I mentioned the fact that the method is likely of limited use when applied genome-wide, because it is likely to produce a large number of false positives.
My comment was:

The accuracy of the method is likely not sufficient to be useful for applying the method on a genome-wide scale, where even a small false positive rate can lead to many erroneous predictions.

The answer of the authors was:

As we demonstrated in the revised version of the manuscript, our method outperforms or is comparable to existing approaches in terms of precision/recall and sensitivity/specificity.

While that may be true, it does not refute my initial comment.  It is very unfortunate that researchers developing methods for sRNA detection choose to use relatively balanced datasets while testing their methods.  This evaluation methodology gives no indication of method usability when used genome-wide (area under the precision recall curve is not invariant to the ratio of positive to negative examples), and can give biologists the wrong impression about the usability of the method.  Furthermore, the majority of the features computed by the authors' method (except for the free energy feature) are insensitive to shifting the region over which they are computed.  That is another reason for the limited usability genome-wide.  Perhaps when combined with a method such as Barman et al, which uses primary sequence, more specificity can be obtained.  Overall, it appears like the problem of sRNA identification directly from genomic sequence is a hard unsolved problem, and this should be indicated.
Additional comments: Minor comments:

- In line 100 n is used to denote the number of negative examples, but in lines 102-105, n is used differently to denote the relative fraction of negative to positive examples.

- In the description of logistic regression you reference "balanced" mode of some implementation of LR, but no mention is made which software was used.  For the other classifiers specific software/version should be mentioned as well.