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: A CROSS-SECTIONAL STUDY OF THE NASAL AND FECAL MICROBIOTA OF SOWS FROM DIFFERENT HEALTH STATUS WITHIN SIX COMMERCIAL SWINE FARMS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript describes the fecal and nasal microbiota composition on a particular group of sows: the ones marked to be removed from the herd in the typical common practice in large farms. Because cull sows remain on the farm, mixed with general population, this analysis is interesting to assess the role of cull sows in the maintenance and re-emergence of pathogens and disease in the farms. The basic idea underneath this study could be evaluated through the microbiota samples taken, however the analysis is out-of-date (qiime 1 is no longer supported since 1/1/18) and there are many concerns that need to be resolved before going public.
The use of English is correct throughout the manuscript.
The raw data is not provided.
The introduction needs more detail and references to state the problem. I suggest to improve the description on previous knowledge on microbiota and diseases in swine. Some examples are:
Espinosa-Gongora, C., Larsen, N., Schønning, K., Fredholm, M. & Guardabassi, L. Differential Analysis of the Nasal Microbiome of Pig Carriers or Non-Carriers of Staphylococcus aureus. PLoS One11 (2016)
Schokker D, et al. Early-life environmental variation affects intestinal microbiota and immune development in new-born piglets. PloS One. 2014;9:e100040. doi: 10.1371/journal.pone.0100040.
Ober RA, et al. Increased microbiome diversity at the time of infection is associated with improved growth rates of pigs after co-infection with porcine reproductive and respiratory syndrome virus (PRRSV) and porcine circovirus type 2 (PCV2) Vet. Microbiol. 2017;208:203–211. doi: 10.1016/j.vetmic.2017.06.023
Gresse R, et al. Gut microbiota dysbiosis in postweaning piglets: Understanding the Keys to Health. Trends Microbiol. 2017;25:851–873. doi: 10.1016/j.tim.2017.05.004.
Recently, a study evaluating both nasal and fecal microbiota of piglets in the farm in the association to the microbiota of their sows should be mentioned and discussed:
Correa-Fiz, F., Neila-Ibáñez, C., López-Soria, S. et al. Feed additives for the control of post-weaning Streptococcus suis disease and the effect on the faecal and nasal microbiota. Sci Rep 10, 20354 (2020). https://doi.org/10.1038/s41598-020-77313-6
Please, be precise when citing. Examples:
Line 63. This particular work describes these changes in nasal microbiota, please specify.
Line 67. “…only focused on healthy sow…” this is not correct for ref [10] which describes the microbiota on piglets.
Line 70. I think this is a study more than a “project”.
Experimental design: The M&M section is well-described in general. However, I find several points that can be improved.
Table 1. Also, include the percentage of each disease (lameness, ulcers, abortion) per farm in the case of compromised culls. The total percentage is included in results section but the info per farm can be relevant to see if the distribution is similar.
Line 109. Which kind of swabs were used? Please, specify so that the experiment is reproducible.
Lines 122-1234 Were the pools done randomly across the 5 animals or was there a reason to pool them? Were the same animals included in the different nasal and fecal pools?
Line 160 Why 94% was used. The typical microbiome analysis uses 97 or 99%.
Line 163-164. The statistical analysis on microbiome data considering the two different variables under study are not described.
Line 168. The analysis can be improved including other diversity metrics, typically used in microbiome studies, such as Shannon. This is the typical metrics to measure diversity and the inclusion could largely benefit the manuscript with interesting results.
Validity of the findings: Line 189 Is the total count of 134,609 is for all the samples or mean per sample?
Line 192 if such a low number was used (done-hundred was used as a cutoff) the results presented should be considered preliminary. This low number is not representative of the composition of the nasal microbiota. Moreover, I would like to see as supp material the number of OTUs per sample.
Line 200 Wouldn’t be possible that the absence of difference is due to the low number of reads analyzed? Discuss.
The differences detected by Chao1 index could be due to the way the richness is estimated based on doubletons.
Lines 206-209. This statement is not correct as it is written. The percentage shown in the plot refer to the percentage of variation explained by each axis of the ordination, but this does not mean this is the percentage of variation between groups, as stated. To obtain this percentage (R2), other tests should be applied, such as Adonis function from Vegan package (Okasnen J, et al. Vegan: community ecology package. R package version. 2015;2:3–0). Please, clarify this or perform the correct analysis to add this info.
Lines 221-226 The way this part of the analysis was done, is not included in M&M section.
Line 228. Why do you state significant differences were observed when you previously have shown that “There was no difference in alpha diversity indices…” (line 200) and “Likewise, there was no difference in diversity indices…” (line203)…? Do you mean that the samples clustered by health status? Are you referring exclusively to richness measured by Chao?
Figure 2. Please, show the statistical differences with stars between the correspondent groups.
Line 240. Idem as before (206-226)
Line 267-272 Remember you are always comparing relative abundance, clarify this in the whole parapgraph. Also, I think it’s worth to mention the relative abundance of the differential OTU found instead of the mean number of reads, as it can be more informative.
Table 3. The title is repeated, the second version is correct.
Lines 254-265 The details regarding microbiota composition are not explicitly shown with their relative abundance values, I would suggest to include this information in a bar plot or as supplementary tables with full information.
The supplemental material is not cited throughout the text.
The discussion section needs to be improved.
Line 292. It is true that few studies have examined the swine nasal microbial diversity. So, in my opinion all should be mentioned. The changes in the nasal microbiota has also been evaluated regarding to antibiotic treatments (https://doi.org/10.1016/j.vetmic.2019.108386 and https://www.ncbi.nlm.nih.gov/pmc/articles/PMC6484018/ ) which I think can have an impact in this study too. Is it possible to know the treatments the sows were exposed? If you don’t have this information, at least you should discuss this issue.
There are some facts that are poorly or not at all discussed in the text:
The study was done regardless the stage of the sows, however pregnancy and lactation can change the microbiota composition at least in humans.
The differences found between farms is shown to differ. The clinical status of the farm should be discussed.
The manuscript would have improved a lot if specific pathogens were particularly searched in the microbiome data.
The analysis is limited to phyla mainly, while most of the differences shown in other papers was at family or genus level. Did you analyze at this taxonomy levels? Include the info or discuss the limited findings.
The fact that a different region from 16S rRNA gene (V4-V5) is analyzed in this study compared to literature (V3-V4), can deeply biased the comparisons. This fact is included briefly but not highlighted.
Additional comments: The data obtained in this study can provide relevant information, however it should be improved a lot the way the analysis is presented to be able to get clear insights into this area.


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: A CROSS-SECTIONAL STUDY OF THE NASAL AND FECAL MICROBIOTA OF SOWS FROM DIFFERENT HEALTH STATUS WITHIN SIX COMMERCIAL SWINE FARMS
Review round: 2
Reviewer: 1

Output:
Basic reporting: Mostly very nice and clear. Just a few, mostly small comments here:
- I couldn't access the raw data by the identifier provided.
- 60: Add year to ref. Sutherland
- 89: Define "commercial" in more detail
- 144: Unclear sentence: WHAT was pelleted and resuspended into what?
- 153: Unclear - the pool is smaller than original samples?
- 192: Clarify the meaning of "filtered"
- 264: Why first part B?
- Fig3: Add captions to a, b ("by farm", "by health status")
Experimental design: I'm happy to see that the data analysis was re-done using current methods. Unfortunately, I'm still afraid that the sample pooling and the partially very small sequencing depths seriously limit the analysis and interpretation of the results.

Using samples with less than 100 reads per pool is highly questionable (I'd be very careful with 1000 reads!). You need to somehow try to validate the analysis results to make sure they are not affected by the very low (and varying) sequencing depths:

- Does the alpha diversity comparison (nasal/fecal) hold if you use rarefaction (or some more sophisticated method) to account for the differences in seq depth? - I'm generally not a fan of rarefaction, but I'm worried when you compare 100 sequences vs 20000 sequences and say that the latter is more diverse.

- Are the PCoAs and other analyses affected by the seq depth differences? I'd generally be very cautious in interpreting the quite weak inter-group differences observed here, especially as the data comes with so many limitations. Also, please check PERMDISP to see whether the reported PERMANOVA results are explained by different dispersions.

- 155: Very nice that you now properly report the use of the negative controls. However, please specify if the blank extractions included empty swabs or were they just empty extractions?
- 169: Why did you use the same number of cycles for both types of samples? The fecal samples are expected to contain much more bacterial DNA (although you quantified the DNA, the nasal swabs likely contain relatively much more host animal DNA).
- 267: Please discuss the reliability of the Nesterenkonia observation (here or in Discussion). Is it realistic to find this genus in this source? Please check the representative sequences for this ASV by BLAST etc.
- 267 & 274: It could be useful to explain the ANCOM results/interpretation a bit, as this is perhaps not the most familiar method for all readers.
Validity of the findings: The manuscript has been significantly improved. I continue to feel that this is an interesting and important topic, but unfortunately the limitations of the data (small N, pooling, and extremely small sequencing depths in the nasal samples) make it challenging to do very many conclusions.

I recommend that the authors consider my remaining critical comments, validate the results of the analyses vs. the limitations of the data, and remove over-optimistic conclusions if they are not really adequately supported by the data.

I think the study still has value as a basic descriptive report for an important field which has not been thoroughly studied. I leave it to the editor to decide whether this type of a report is suitable for PeerJ.
Additional comments: I'm happy to see that the authors have utilized the reviewer comments to significantly improve the manuscript. It's a pity (but understandable at this stage) that it's not possible to add more actual data to the study (individual analyses of animals, etc.). I hope the study will be published here or in another journal, as it does provide useful baseline information for pig research.


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: A CROSS-SECTIONAL STUDY OF THE NASAL AND FECAL MICROBIOTA OF SOWS FROM DIFFERENT HEALTH STATUS WITHIN SIX COMMERCIAL SWINE FARMS
Review round: 3
Reviewer: 1

Output:
Basic reporting: Just a small typo on line 210/217: "generates generate".
Experimental design: All other issues have now been addressed, but some major problems remain in the analysis of nasal samples. I didn't previously realize that these were indeed rarefied down to 66 reads. This is really very, VERY small number of reads, and I don't think I've ever seen anybody try to perform a meaningful analysis at such a level (although this problem is not unfamiliar in our own work!). It may still be worthwhile to report these data, but the major limitations need to be still more thoroughly and openly addressed:

- Report clearly the distribution of read depths in nasal samples (at least, medians and standard deviations per experimental group; preferably also for every individual sample e.g. in supplement)
- Depending on the number of samples with adequate read depths (let's say, >1000 or at least >500, really depending on how the analytical results behave), consider omitting even more low-depth samples
- Re-run the analyses without rarefaction, as rarefying to such extremely low level will delete most of your data; compare and discuss the results obtained by either way
- Remove or carefully discuss ALL comparisons possibly affected by this limitation (such as, nasal vs fecal microbiota; also critically evaluate the reliability of nasal microbiota comparisons between experimental groups etc)
- Based on these, discuss the nasal microbiota data still more critically
- Also critically discuss the uncertainty of not analyzing empty swab negative controls vs. the very low read depths in nasal samples

Note: I would be VERY happy to see a 16S qPCR comparison of nasal samples vs. extracts from empty swabs - this would not be a big deal to do, and would considerably contribute to the reliability of the data.
Validity of the findings: See part 2.
Additional comments: Many thanks for considering the reviewer comments and again improving the manuscript. I also highly appreciate providing the revisions in several clear formats to the reviewers, making our job easier.

I apologize for not fully realizing the issue about nasal sample sequencing depths and rarefaction prior to this revision. Based on the PeerJ guidelines, I need to classify this as a major revision, as it may affect interpretation of results, requiring one more round of review.


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

Input:
Title: A CROSS-SECTIONAL STUDY OF THE NASAL AND FECAL MICROBIOTA OF SOWS FROM DIFFERENT HEALTH STATUS WITHIN SIX COMMERCIAL SWINE FARMS
Review round: 4
Reviewer: 1

Output:
Basic reporting: -
Experimental design: Thank you for the additional information on the effects of low read counts and rarefaction. However, I'm afraid I still cannot accept the statistics in the present form. Please re-do all statistics like I already suggested:

- Exclude all samples <500 reads from all analyses. Even this is a VERY low threshold, probably considered much too low for many experts. Below that, it's really not appropriate to perform any meaningful analyses.

- Perform rarefaction to 500 reads in Alpha diversity analyses. It is impossible to reliably compare alpha diversity indices for samples with 500 and 50000 reads (and it's quite obvious that nasal and fecal samples seem different because of this). For other type of analyses, I recommend using the full data (without rarefaction).

- It was very nice for the reviewers to see the effects of various ways of data processing (rarefaction or not, exclusion or not). But it is not very useful to the reader and makes the results more complicated to read. So please report only one version of results, based on an acceptable data analysis (as suggested above).

I still believe a qPCR analysis would nicely complement the results for low-biomass samples, even if the negative control swabs would be from a different lot.
Validity of the findings: see above
Additional comments: I'll be happy to do the full re-review when you provide the properly done statistics.


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: A CROSS-SECTIONAL STUDY OF THE NASAL AND FECAL MICROBIOTA OF SOWS FROM DIFFERENT HEALTH STATUS WITHIN SIX COMMERCIAL SWINE FARMS
Review round: 4
Reviewer: 2

Output:
Basic reporting: Comments addressed
Experimental design: Comments addressed
Validity of the findings: Comments addressed
Additional comments: Most of the issues previously raised have been explained and solved out.

Typo in line 240-241 “…with a range of  of 1-27,870 reads prior to…”

There is still a sentence that needs to be corrected:

Lines 312-316 when explaining the work of Correa-Fiz et al 2019, the sentence is not correct. IN this study, the use of antimicrobials is compared in the same farms in a period using peri-natal antimicrobial treatment and after, when this treatment was not done at all. So the correct sentence would be:

A study conducted in Spain reported the use of peri-natal treatment with antimicrobials (including penicillin, streptomycin and tulathromycin in one farm, and ceftiofur and tulathromycin in a second farm) in 3-4 week old piglets to be associated with a decrease in nasal microbiota diversity as compared to a period without using these peri-natal treatments.


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: A CROSS-SECTIONAL STUDY OF THE NASAL AND FECAL MICROBIOTA OF SOWS FROM DIFFERENT HEALTH STATUS WITHIN SIX COMMERCIAL SWINE FARMS
Review round: 5
Reviewer: 1

Output:
Basic reporting: All my concerns have now been sufficiently addressed. Well, some of the texts in the figures are tiny and some of the colors in the figures difficult to distinguish from each other.
Experimental design: All my concerns have now been sufficiently addressed.
Validity of the findings: All my concerns have now been sufficiently addressed.
Additional comments: All my concerns have now been sufficiently addressed.


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

Input:
Title: VARIABILITY IN DEER DIET AND PLANT VULNERABILITY TO BROWSING AMONG FORESTS WITH DIFFERENT ESTABLISHMENT YEARS OF SIKA DEER
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript is clear, although several word choices are problematic (see general comments). The introduction presents the concept clearly, although some clarifications are required (see detailed comments in the attached PDF). The figures and tables labels provide insufficient information and need to be expanded to be more self-standing. Here’s some of the things I would need to see added either to the figures or to their captions:
•	Figure 1: What are the numbers on the map? The sites? The distance scales only show two subdivisions, at an ineligible font size, making them of little help.
•	Figure 2: What statistical test was used to produce the different grouping? What alpha level? Which deer species? How many plots in each category of establishment years?
•	Figure 3: What does an NMDS stand for? How many species considered? How many sites? What does the ‘stressed = 0.21’ at the top of the graph means? What are the labels?
•	Figure 4: What are those groups? What do they represent? What does MDF stand for? Axis could also be adjusted for less white space at the top
•	Figure 5: How many deer/samples? Which deer species? Again, what is this ‘stress = 0.23’ at the top of the graph?
•	Tables : More information on the statistical analyses in the captions are required, and sample sizes and degrees of freedom are needed
Yes, adding this information would make repetitions from the method section, but making the figures self-standing will improve the manuscript, and especially the clarity and ease of reading.
Experimental design: This manuscript report primary research in the scope of PeerJ. The subject is interesting and relevant : the authors use a chronosequence of sika deer establishment eras to evaluate their effect on plant community cover and diversity. They also use feeding traces and deer feces to evaluate how use of plant species varies among regions with different establishment eras. The methods seem appropriate, and although I’m not aware of the standards regarding metabarcoding analyses, this seems to be well explained and appropriate. The appendices, however, could be improved for clarity (e.g. ‘we sampled the leaves of those plants’, without precision about what are those plants.). The authors should remember that it is an independent document, and asking the reader to go back and forth between two documents to understand it too much. I’m also surprised by how few references are cited in the appendix.
I have one main issue with the experimental design, in regards to the evaluation of feeding trace. Feeding traces (both browsing and grazing) were evaluated in one season, which could influence the detectability of traces. For example, if the browsing occurred in the previous winter, browsing trace on woody plants will be much harder to evaluate in the fall. I’m also wondering how the four classes of damage used can be applied to grazing on forbs and grass. I’m suspecting that this method of damage evaluation presents a strong bias among plant life forms, suggesting that the following analyses comparing life forms are biased.
Validity of the findings: This is my main concern regarding this manuscript: I do not think the interpretation and conclusions are supported by the results. This dataset is a chronosequence based on deer establishment eras, and while this type of study is useful to trace back the effect of a perturbation, the authors go too far when they extrapolate changes in deer selectivity (wrongly called palatability) among these eras.
First, those eras are very variable in size and relatively uncertain, which is obscured by the phrasing of ‘establishment year’. The second class (‘2003’) is especially large, which represent deer establishment between 1979 and 2003. The very recent (2012-2014) and very old (1978) make for a more certain comparison. Second, we have no information about the vegetation cover, composition or state before establishment. This is a very strong assumption to make that the only thing affecting vegetation changes between 1978 and 2014 is deer establishment. The authors briefly acknowledge this in the discussion, but don't really adjust their conclusions. One element of deer selectivity that is not discussed in this manuscript is how the species composition, not only the diversity or richness, can influence food choices (for example: Champagne et al. 2018). Differences in initial composition or vegetation state could have made for different trajectories in deer impacts on the ecosystem. Finally, the feces were collected once, in a seasonal ecosystem. This strongly limit the inferences that can be made on deer diet.
This doesn’t undermine the good research that was done here, but I do think the authors need to revise their conclusions. The leap to changes in forage selection is too big and the authors should be more careful in their interpretation. They also cannot infer to the tolerance of these species. Tolerance is the regrowth process following damage, and the authors rather evaluate the persistence of species in a chronosequence. The last paragraph of the discussion regarding the use of indicator species could be an interesting outcome of this study, but the link to the actual results is thin and could be clarified.
Other smaller points:
•	The authors should verify if their use of Mantel test is appropriate or not based on Legendre et al. (2015).
•	I tried running the code provided by the authors, and it didn’t work. I suspect the mistake is only minor: the plant_site.csv data provided has 276 variables and the first coding line selects columns from 7 to 292, which is impossible. I also don’t know what the columns name stand for.
•	The sentence in lines 373-375 simplifies too much sika deer forage selection. Although plant density does affect forage selection, the support for plant apparency in mammalian herbivores is dubious… while reduced apparency can increase the time to browsing, the most profitable resources are generally consumed in the end (Stutz et al. 2015, Stutz et al. 2017). Also, there’s no surprise in not seeing a clear pattern for one plant category or another, as the nutritional value and chemical content of individual species are very determinant in forage selection (Examples of Cervus nippon selection based on chemical content can be found in Champagne et al. 2020).
Additional comments: As pointed out in a previous section, I disagree with the use of certain terms. First, palatability is a very vague concept and the authors should define it or rather use a more appropriate term. Are they referring to the chemical composition, the chemical value or to the use or selection by sika deer? I suggest reading the classic Johnson (1980) for an appropriate use of the latter. It’s especially important for this manuscript to use the proper terms, because I doubt plant palatability actually changed. It’s the behaviour of the animals that potentially did, and what they consider to be an acceptable resource, depending on what is available.
The authors also frequently refer to ‘vegetation’ but it’s not what always clear what element of vegetation community is referred to. For example, in lines 17-18: ‘the differences in plant palatability and vegetation among different stages’. Are we talking about changes in composition, diversity, growth rates, abundance (the ‘coverage’)? The ‘number of plant species’ is actually the richness.
References
Champagne, E., A. Dumont, J.-P. Tremblay, and S. D. Côté. 2018. Forage diversity, type and abundance influence winter resource selection by white-tailed deer. Journal of Vegetation Science 29:619-628.
Champagne, E., A. A. Royo, J.-P. Tremblay, and P. Raymond. 2020. Phytochemicals involved in plant resistance to leporids and cervids: a systematic review. Journal of Chemical Ecology 46:84-98.
Johnson, D. H. 1980. The comparison of usage and availability measurements for evaluating resource preference. Ecology 61:65-71.
Legendre, P., M. J. Fortin, and D. Borcard. 2015. Should the Mantel test be used in spatial analysis? Methods in Ecology and Evolution 6:1239-1247.
Stutz, R. S., P. B. Banks, N. Dexter, and C. McArthur. 2015. Herbivore search behaviour drives associational plant refuge. Acta Oecologica 67:1-7.
Stutz, R. S., B. M. Croak, N. Proschogo, P. B. Banks, and C. McArthur. 2017. Olfactory and visual plant cues as drivers of selective herbivory. Oikos 126:259-268.


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: VARIABILITY IN DEER DIET AND PLANT VULNERABILITY TO BROWSING AMONG FORESTS WITH DIFFERENT ESTABLISHMENT YEARS OF SIKA DEER
Review round: 1
Reviewer: 2

Output:
Basic reporting: Authors report on a field study aimed at understanding deer diet at sites that differ in time since deer establishment.  At each site, researchers documented understory plant communities and feeding traces on target plant species. In addition, they use DNA barcoding techniques to identify plant species consumed by deer and present in their feces. Results indicate a significant shift in plant communities and deer preferences according to time since deer establishment.  The results may expand our understanding of deer impacts and inform management.  Before publication data analyses should be revised.  Please see my comments below.

1.	Please develop hypothesis and predictions for the study and include them at the end of the introduction
2.	I suggest authors review newer literature. For example, most papers cited on lines 33-39 are more than 20 years old. Newer literature has summarized current impacts of ungulate introduction or increased abundance. Similarly, on line 49, although there are technical difficulties with density models for deer, there are newer applications and developments.
Experimental design: 1.	Lack of independence in statistical analyses.  How did authors account for the lack of independence among quadrats within the same site? It is not clear, if they entered a single value per site or all replicates per site.  Replicates within the same site are not independent and treating them as independent would violate model assumptions.  Please clarify and/or re-run analyses to avoid violation of independence assumption.  Same consideration applies to species richness, diversity indexes and PERMANOVA analyses.
2.	Several tests were performed, but the purposes of each is not clear, nor why certain PERMANOVA were conducted twice (both with the same response variable).  The reasoning for each analysis is not clear. Please revise writing of this section
Validity of the findings: 1.	Given the ambiguity in the analysis, it not possible to evaluate the validity of findings. Findings might change once analyses are re-run to account for lack of independence among samples or the text is clarified.
2.	As described, the methodology of the feeding trace component cannot determine if feeding was due to deer browsing or other herbivores.  Also, it is not clear how local abundance of each species was determined. I suggest authors clarify the writing and describe how they excluded herbivory by other mammals (for example, rodents).  If consumption by other herbivores was not recorded or separated during data collection, this section needs to be revised.
Additional comments: 3.	L56-58 Please revise language. Meaning is not clear
4.	L103: should be “all area in Japan is divided”, not “are divided”. There is another example with verb agreement on line 164 (were applied not was applied). Please revise the whole document
5.	L107: can authors explain why did they not select sites within category 5.  Wouldn’t absence of deer be considered a control or reference for vegetation communities?
6.	L114-115: was each site sampled twice or just once? If only once, were sites sampled on different years, and how was this accounted for? Where all sites 500x500m?
7.	L120: while ferns are not regularly eaten by deer, their abundance may increase under high deer abundance. In North America high fern abundance is associated with increased deer activity.  Authors should discuss this aspect and review literature regarding fern abundance
8.	L126: By convention, numbers at the beginning of a sentence should be spelled (ten not 10)
9.	L129: were individuals selected at random? Was the whole area (500 x 500 m) sampled? How far apart were individuals? Please specify. Also, specify how you estimated average plant height. Wouldn’t height be affected by deer activity? And consider reporting the average plant height at each site in the supplementary
10.	L124 and related text: clarify that feeding damage is not deer damage. The feeding damage may have been produced by any herbivore.
11.	L134-135. How was the total number of ramets at each site estimated? Was this estimated for the whole area site? Please provide details
12.	L184-192. Please clarify which plant data you used for these analyses. Is it the understory vegetation? If it is only about the vegetation survey, why are two PERMANOVAs required?
13.	L224: proportion should not be capitalized
14.	L254-259. Is there one site per year-of-deer-establishment category? Or is this a typo? Also, provide evidence for claims of abundant plants, feces and trails. What is abundant? What was considered unpalatable? Report abundance of said species and provide examples or refer to supplementary table. Any analysis to support these claims?
15.	Fig. 1. Please revise caption. Figure has a panel a and b, but there is no reference of that in the caption. Also, indicate that site number is correspondent to Table S1, which provides all the information about each site. Indicate in legend that categories represent years since deer establishment and identify the site at which picture was taken
16.	Fig. 2. Indicate number of replicates in caption
17.	Table S1: x and o symbols are confusing.  I suggest replacing by 1/0, detected/not detected or yes/no. Also, include a brief description of the procedure used to detect feces
18.	There is not Table S2 in supplementary file


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: VARIABILITY IN DEER DIET AND PLANT VULNERABILITY TO BROWSING AMONG FORESTS WITH DIFFERENT ESTABLISHMENT YEARS OF SIKA DEER
Review round: 2
Reviewer: 1

Output:
Basic reporting: The reporting of this study is generally up to the level required for publication. Some of the added/modified sentence can be a little difficult to read and should be revised.

There's also a small issue with the changes from 'palatability' to 'selectivity' which I discuss in the general comments.

While the raw data and code is shared, the code does not run (see section 3).
Experimental design: No comment.
Validity of the findings: The changes made to the manuscript add to the manuscript a good discussion of the study limitations.

However, the answer to my comment 6 has left me perplexed : 'We did not include degree of freedom because it corresponds with the sample size.'. We are talking about mixed models with a blocking structure, in which case I highly doubt that the degrees of freedom equal the sample size. Moreover, if we take the example of Table 1, this would mean there's a big issue with the determination of statistical significance, because the critical value for a chi-square distribution with a sample size of 440 is 489...and none of the presented results would be significant.

What the authors are reporting here are the results of the a posteriori test within a significant main response variable (aka life form and plant architecture). They need to report the statistics associated with the response variable (probably an F value) with the appropriate degrees of freedom (numerator and denominator).

I actually tried to run the authors code to provide them guidance on how to obtain this information. The code is not working past the line 15.
Additional comments: In general, I am satisfied with the changes made to this manuscript and to the answers provided to my previous comments.

One of my suggestion, however, was perhaps poorly described and led to some confusion. The change to 'palatability' to 'selectivity' everywhere doesn't work. Actually, the authors mean 'selection' much more often than they mean 'selectivity'. Selectivity is the degree of selection done by the deer (is it a picky eater or not), while selection is actually what was consummed. In some occurence, selectivity should be changed to selection. See example in line 96.
In others, the authors actually 'vulnerability' or 'susceptibility', that is the risk experienced by a plant species of being browsed. See example in line 58.
Finally, the first paragraph of the discussion talks about preference. Unless you have the availability of the resource, this is not preference, this is selection. To measure preference, you would need equal availability (See Johnson 1980). This is the case in lines 380-382.

Two very minor details:
L 141-143 : Perhaps explain how rabbit traces differ from deer for unaware readers.
L 305-306 'A spatial autocorrelation was not detected as none of the vectors (MEMs) were detected significant.': Bulky sentence. Rather try: We did not detect spatial correlation, as none of the vectors (MEMs) were statistically significant.


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: MODEL FOR FINDING THE NUMBER OF HONEY BEE COLONIES NEEDED FOR THE OPTIMAL FORAGING PROCESS IN A SPECIFIC GEOGRAPHICAL LOCATION
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors used a clear and unambiguous professional English throughout the manuscript. I suggest adding some citations and literature references to support some statements and fulfill background/context information.
This manuscript sheds light on solving an important problem for beekeeping. I understand that this is not a definitive and precise model, but it has its finding and in the future can help to improve the productive levels in beekeeping. I missed a well-elaborated discussion comparing it with other relevant works dealing with the same theme, as well as comparing it with other techniques for estimating the ideal number of colonies per apiary.
Experimental design: The research question is well defined, relevant and significant. However, for the future, it would be interesting to validate it in real life, choosing some apiaries to estimate the ideal bee colonies. In general, methods are described in sufficient detail and information to replicate. Furthermore, math models leave possibilities for adding more variables that may be necessary to refine the calculation in another region or depending on the context.
Validity of the findings: The conclusions are well presented, linked to the original research question, and limited to supporting results. However, I would suggest the authors better define what does this mean: “the number of bee colonies needed for the process of ideal foraging”. Does it refer to honey production or colony maintenance? Some claims sound like ordinary beekeeping procedures or even speculation rather than a scientific method. Please add solid and recent references to support these statements.
Additional comments: - Scientific name must be in italics - Apis mellifera
- Please add references to support some statements in the Introduction Section e.g. " ...location usually is based on beekeepers’ experience or the limited availability of physical space." (lines 48-49), "..In most cases, success in beekeeping depends on the availability of sufficient bee foraging resources in
terms of both quality and quantity of nectar and pollen." (lines 64-65)
- In the Introduction, the authors use examples for honeybee colonies densities that occur naturally in forests. This number can vary widely from biome to biome and from agroecosystem to agroecosystem. So, apiaries mean colonies managed by beekeepers. Thus, I would suggest the authors use examples of carrying capacity of areas for colonies managed in apiaries to be closer to the objective of this work.
- Line 50-51: This statement is confusing. There is a vast literature that defines the number of bee colonies per area that must be introduced into a field/orchard or plantation to maximize production through pollination, according to the biology of the crop species. Please see Delaplane et al. (2013)- Standard methods for pollination research with Apis mellifera. So, please, consider rewriting this statement.
- Please provide a citation and some evidence to support this number of 0.35, further explaining what this bee foraging efficiency index would be. Would it be the ratio of energy gained to energy expended to acquire food? Is this related to the Optimal Foraging theory? Please, provide more details.
- Fig 9d and Fig 9e: What is the relevance of these variable/map for the formula? Please, explain better. Provide more details.
- In Section 3.9. Calculation of a number of colonies to be placed at a specific location (x,y), the authors should explain the calculation step by step and add discussion to it. Compare with other previous publications and different techniques that estimate the optimal number of colonies for an apiary. Improve this section!
- The numbers in the figure captions are different from the figure numbers in the body of the text. So check everything again, choose the most suitable one and align the number in the Captions to the body of the text.


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: MODEL FOR FINDING THE NUMBER OF HONEY BEE COLONIES NEEDED FOR THE OPTIMAL FORAGING PROCESS IN A SPECIFIC GEOGRAPHICAL LOCATION
Review round: 1
Reviewer: 2

Output:
Basic reporting: 1. While the manuscript is written in an understandable manner, there are some issues with the English. The use of articles (e.g. in the title "in the specific geographical location" should be "in a specific geographical location"), in particular, should be reviewed. There are other instances where phrasing could be better (e.g. in line 71 - "the previous author model" could instead be written "the authors' previous model"; in line 88 - "road effect on the foraging activity" could be written "effect of roads on foraging activity").

2. Some of the notation used in the equations is, to my experience, non-standard. In particular, equations (8) and (9), which I believe to be denoting functions transforming fields and roads into polygons and lines respectively, should be written using more widely used standards of notation (e.g. https://en.wikipedia.org/wiki/Function_(mathematics)#Notation ).

Moreover, the notation for discrete uniform distributions "R" (first introduced in line 232) is non-standard (see https://en.wikipedia.org/wiki/Discrete_uniform_distribution ). Replacing "R" with the standard "U" notation would be especially helpful given that R is also used in line 265 to represent "roads from regions of interest".

3. Explanation of all variables in equations should be provided. For example, what is P_n in equation (8)?

4. Typo in line 261: "," in "-0,1" should be a ".".

5. Though it builds on previous work by the authors, the work is self contained. Sufficient background literature is provided. The figures are clear.
Experimental design: 1. The formulation of "optimal foraging performance" seems slightly off. In like 45-47, the authors describe the number of hives that gives "optimal foraging performance" as the "number of colonies placed at one geographical location (within one apiary)" such that "[the colonies] should be able to forage the maximal amount of potential resources available". I believe this definition to be incomplete as, under said definition, the number of hives can increased indefinitely until all the potential resources are used up (that is, the colonies forage the "maximal amount of potential resources available" once they forage all available resources). I reckon the definition should be revised to be more in line with the definition of "optimal location" seen in the authors' previous work (Komasilova et al., 2020): "optimal location will allow bee colonies to forage on higher amount of the resources with minimal  energy consumption." (the key bit being the minimisation of energy consumption).

2. The authors tackle a problem that is meaningful to beekeepers. The method proposed seems sensible. Code is provided and the description of the method is detailed.
Validity of the findings: The model is evaluated on dummy data and has not been evaluated under real-world conditions. It is thus difficult to say how well the model proposed by the authors would function in practice. This limitation is mentioned by the authors.
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: MODEL FOR FINDING THE NUMBER OF HONEY BEE COLONIES NEEDED FOR THE OPTIMAL FORAGING PROCESS IN A SPECIFIC GEOGRAPHICAL LOCATION
Review round: 1
Reviewer: 3

Output:
Basic reporting: The presented manuscript addresses a relevant question in modern beekeping. The general readivility can be improved if more attention is paid to lenguage details. Some phares can be improved by adding puntuation marks.

The presented background is generally good, althouhg it can be improved making more enphasis on why the research is needed. For example, some lines can be added to explain what is the current problem when honeybee hives are introduced without a proper knowledge of the carrying capacity of the landscape.

The section matherials and methods can use a major transformation to facilitate its readibility as the current version is difficult to follow. Equations are not referenced in the main text and some terms are not defined. Hence it is not clear the meanining of the equations. I suggest the authors to consult the existing litterature presenting related models (for example the beehave model) to get an idea on how a model can be propertly described. In general, further work is needed to improve the flow of this section.

The section results and discussion are not property labeled. In this section the model was further described and presented with an example. This information should be in the section of materials and methods rather than in results and discussion.
Experimental design: The research question is well defined, relevant and meaninigful. With some exta work, it can clearly state how this research fills the identified knowledge gaps. However, the content of the manuscript does not seems to represent a thorough research. It does not have a propertly stablished result section and it does not have a discussion sections that frames the current work in the litterature (existing models, implication of finidings, concrete further research).
Validity of the findings: The impact of the research in the current scientific context is not assessed. The presented work is not replicable under the current model description. It is not explained how the values used in the model were obtained. In order to make the model replicable, further work needs to be done for improve the flow of the description.

The research lack results and discussion to elaborate further the conclusions.
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: EVIDENCE FROM THE RESURRECTED FAMILY POLYRHABDINIDAE KAMM, 1922 (APICOMPLEXA: GREGARINOMORPHA) SUPPORTS THE EPIMERITE, AN ATTACHMENT ORGANELLE, AS A MAJOR EUGREGARINE INNOVATION
Review round: 1
Reviewer: 1

Output:
Basic reporting: The study of Paskerova et al. is an important contribution to the morphological and molecular evolution of eukaryotic unicellular organisms from the phylum Apicomplexa. It is clearly and professionally written, authors have very good literature overview and expertise in studying apicomplexans from the class Gregarinomorpha. Figures are of excellent quality, well labelled and described. They are real eye-catchers.

Custom checks requested by Editor
- Authors provided DNA data deposition statement, including the GenBank accession number (MT214481). The data are, however, not available yet and will be released after publication according to the NCBI webpage.
- Authors did not describe any new species. They emended diagnoses of one species-group taxon (Polyrhabdina pygospionis) as well as of some higher taxa (i.e., Ancoroidea, Polyrhabdinidae, Polyrhabdina). Authors also established a new family, Trollidiidae. Its proposal meets standards of the ICZN (1999). Following Recommendation 8A of the International Commission on Zoological Nomenclature (2012), authors also provided the ZooBank registration number of the work. Although not obligatory, I also recommend to provide the ZooBank registration number of the act (establishment of the family), which was automatically generated when the new family-group name was registered.
Experimental design: The manuscript includes original primary research, with well defined questions. Morphological methods are state-of-the-art, they are well described. Molecular phylogenetic methods are standard and could be described in more detail and additional analyses should be conducted (please see General comments for the authors).
Validity of the findings: The characterization of Polyrhabdina pygospionis is of excellent quality. I am also convinced by the argumentation that epimerite represents the major morphological innovation of eugregarines. I also find the Taxonomic summary reliable, although statistical support for monophyly of the Ancoroidea is very poor (not strong as stated by the authors). Anyway, I do not see a problem in emendation of the diagnosis of the Ancoroidea, as this name is already available. Likewise, names of all other taxa treated in the 'Taxonomic summary' section are already available except for the Trollidiidae, which are established as a new family-group name. Trollidium obviously represents a very distinct evolutionary lineage within the Gregarinomorpha, so I do not see a problem to name its cluster.
Additional comments: Specific comments

- M & M - I would recommend to apply also a different alignment and masking strategy. For instance, authors can use the Mafft algorithm implemented in the Guidanace2 server and try different cut-off values to mask columns with certain confidence scores estimated by the alignment algorithm. It is much less subjective that to apply own masking strategy in BioEdit. At least five different cut-off values should be tried to see the robustness of results after building trees. Authors can compare these results with their own strategy and will see whether the aligning and masking strategy might have an impact on subsequent phylogenetic inferences.
It is not clear to me whether 5.8S rRNA gene sequences were treated as a separate partition or together with 28S rRNA gene sequences. 5.8S is rather short and has a very different evolutionary rate than 28S. Were partitions considered also in the ML analyses conducted with IQ-Tree? I find 100 bootstrap replicates to be very few. A minimum is 1000 bootstrap replicates to obtain reliable results. A rapid bootstrapping can be applied, but then different support thresholds apply.
I also find two phylogenetic methods to be insufficient, especially when the resolution in the deeper parts of trees is so poor. I do understand that this might be due to the lack of phylogenetic signal in the data, but I suggest to test this. There are also other ML (PhyML, RAxML) and Bayesian methods (PhyloBayes, Phycas) that could be employed for tree inferences.

- Results (Phylogenies inferred from rDNA sequences) - Authors incorrectly interpret statistical support values. Bootstrap values <70% are low, 70–94% are moderate, and ≥95% are high (Hillis, D. M. & Bull, J. J. 1993. An empirical test of bootstrapping as a method for assessing confidence in phylogenetic analysis. Syst. Biol., 42:182–192.). For the Bayesian posterior probabilities, values <0.94 are statistically insignificant and ≥0.95 are significant (Alfaro, M. E., Zoller, S. & Lutzoni, F. 2003. Bayes or bootstrap? A simulation study comparing the performance of Bayesian Markov Chain Monte Carlo sampling and bootstrapping in assessing phylogenetic confidence. Mol. Biol. Evol., 20:255–266.).

- Fig. 6 and 7 - please label archigregarines, blastogregarines etc.

- Diagnoses of taxa contain information (number of taxa included, monotypic etc.) that is not "diagnostic at all". Please remove it from there and transfer to remarks. Remarks to the superfamily Ancoroidea - it is not a well supported rDNA lineage (I see that there is post. probability 1.00, but 56% ML bootstrap. We cannot trust in such a lineage from a phylogenetic point of view).

Minor comments
line 54 - Ancoroidea Simdyanov et al., 2017 [please insert a comma, check this also in figure legends]
line 63 - Apicomplexa are [The Latin noun Apicomplexa is in plural, for instance Aves -> plural, we do not say "birds" is...]
line 310 - BP=56% is not moderate, it is very weak
line 320 - BP = 77% cannot be considered as strong, at best it can be considered as moderate
line 323 - posterior probability 0.94 is not high at all, it is statistically insignificant, BP <50% is nothing...
line 556 - Type family. Ancoridae Simdyanov et al., 2017 [please insert a comma]
line 563 - please delete "One to three genera." This adds nothing to 'Diagnosis' of the family.
lines 570-571 - please delete "Seven named species." This is not a diagnostic character. Maybe put this information to remarks and list all seven species.
line 609 - Please provide also ZooBank Registration of the act


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: EVIDENCE FROM THE RESURRECTED FAMILY POLYRHABDINIDAE KAMM, 1922 (APICOMPLEXA: GREGARINOMORPHA) SUPPORTS THE EPIMERITE, AN ATTACHMENT ORGANELLE, AS A MAJOR EUGREGARINE INNOVATION
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper is overall quite well written. I think it has many good qualities.
Experimental design: The paper has a good experimental design. It is a bit far-reaching with its conclusions in some places, based on the data presented, however.
Validity of the findings: Again, I think that the major flaw with this paper is that the conclusions, while well-stated, are far-reaching, and maybe need to be toned down a bit to better match the results. I think the authors are riding that line of speculation quite hard.
Additional comments: The manuscript entitled “Evidence from the resurrected family Polyrhabdinidae Kamm, 1922 (Apicomplexa: Gregarinomorpha) supports the epimerite, an attachment organelle, as a major eugregarine innovation” introduces new systematic organisations to gregarines, and also discusses some of the evolutionary history of the group, in particular the epimerite of eugregarines.

In general, I found the manuscript to be quite good. I do think it deserves to be published. The quality of the data is high, and I think the points brought up in the paper are interesting and are of academic significance to the field of gregarines which are poorly understood.

My major issue with the manuscript has to do with the introduction of new families, based on the molecular data presented in this paper. The trees generated from the ribosomal operon of gregarines are just not resolved at the appropriate nodes to use this information to support changes to systematics and classification of the group at the family level (in my opinion). Looking at the trees, support for Ancoroidea (including Trollidium) is 1.0/56 and the next node down is 0.98/32. It is just not great support. I know that the reduced-taxon tree shows 0.94/90, and 1.0/75, but this could also be a relic of long branch attraction. These branches are some of the longest on the whole tree of eukaryotes. I propose that perhaps we can get more taxa in these larger, multigene datasets and make more informed decisions on the families and genera at that time, rather than changing things repeatedly and just causing increased confusion in the field. One of the section headings in the paper reads “Ribosomal DNA supports the family Polyrhabdinidae and the emended superfamily Ancoroidea.” I just don’t think the data supports it that strongly.

Nonetheless, I think that the paper has some interesting points, and the data really is of high quality, so I think it should be published. I just want to avoid having superfamilies introduced every time we publish a new gene. It could get quite tedious. But I will leave that to the editor to make the final decision.

Best,

Kevin Wakeman


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: EVIDENCE FROM THE RESURRECTED FAMILY POLYRHABDINIDAE KAMM, 1922 (APICOMPLEXA: GREGARINOMORPHA) SUPPORTS THE EPIMERITE, AN ATTACHMENT ORGANELLE, AS A MAJOR EUGREGARINE INNOVATION
Review round: 2
Reviewer: 1

Output:
Basic reporting: The study of Paskerova et al. is an important contribution to the morphological and molecular evolution of eukaryotic unicellular organisms from the phylum Apicomplexa. It is clearly and professionally written, authors have very good literature overview and expertise in studying apicomplexans from the class Gregarinomorpha.
Experimental design: The manuscript includes original primary research, with well defined questions. Morphological methods are state-of-the-art, they are well described. Molecular phylogenetic analyses were very carefully conducted, the effect of various alignment and masking strategies on tree inferences was adequately addressed.
Validity of the findings: The characterization of Polyrhabdina pygospionis is of excellent quality. The argumentation that epimerite represents the major morphological innovation of eugregarines is very convincing. Taxonomic summary is consistent and well prepared.
Additional comments: Dear Authors,

I am highly satisfied with the revision! All my concerns were appropriately addressed. I am also very happy to see that phylogenetic analyses were moved to superior level. In my opinion, the present multifaceted phylogenetic approach added a lot to the future strategies of tree inferences in Apicomplexa and can serve as inspiration for other researchers.

Congratulations!


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: GNRH OR ESTRADIOL BENZOATE COMBINATION WITH CIDR IMPROVES IN-VIVO EMBRYO PRODUCTION IN BOVINES (BOS INDICUS AND BOS TAURUS) UNDER SUBTROPICS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Dear Editor,
The present review concerns the manuscript: “GnRH or Estradiol benzoate combination with CIDR improves in-vivo embryo production as compared to conventional superovulation in bovine (Bos indicus and Bos taurus) under subtropics”. It is an interesting topic where the authors propose something new in terms of new knowledge in the area of embryo transfer.
However, in my view, the authors were unable to expose the data with sufficient clarity to approve the manuscript.
The title could be improved.
Abstract:
Insert how many animals were allocated in each group;
I couldn't find out if it was 70 cows or 90 cows?
Which breeds were crossbred cows?
The abstract was very confusing (relative to the control group), because it was difficult to know if they received FSH or not .... This has to be well specified.
Was the superovulation done in just one moment ( same time)  or in several moments?
P.7- L.41: Both groups were given SO of 11o. on the 13th day. However, elsewhere, the control also received (p.7, L48-49). He's confused.
p.7 - L 49: 90 cows? It is necessary to clarify
p.7-L50-51: phrase out of context. Add in the methodology;
What is “nondescript recipient?
Ovarian structures? What is? Specify which structures?
Again -….number of animals per group?
P.7 L52: what does super estrus follicles mean?
In the abstract: results are missing or poor described;
P.7 Substantially lower: what is it?
P7. - L55: enter the p value. The p value is missing from the table as well.
P7. 56-58: Confused. To clarify
P7 - L 62-65: improving the conclusions
P7 - L77: non descript animals? What is that?
P8- L88-89: references are missing
P.9-L114: total animals (70 or 90 cows)?
P.9-L129: on on ??? what is this?
P21 - There is a lack of incomplete legends in the figures;
Give a number to the figures
P26: what kind of animal it was (figure captions)
Table:  should be opened. There is no vertical line in the table
Table 1: symbols are missing from the variables (or % or “n”). Say what specie is ? (cow)
P10- L136: what is super estrus?
Table 1 - clarify better
No Abstract. embryos there is no mention of frozen embryos;
I could not observe the pregnancy rate of the transferred embryos. Place on the table. Will be better.
P 13- L 241- Reference: MS Khan, 2002 is not used.
Pregnancy rate of groups? where?
Table 1 legend needs to be improved (legend will go below)
Was the cows heat induced or were submitted to estrus synchronization for superovulation?

Mr. Editor,
The English language is not within my competence, but there are deficiencies in the English language.
Experimental design: See please, my general commentaries.
Validity of the findings: See please my general commentaries
Additional comments: Dear Editor,
The present review concerns the manuscript: “GnRH or Estradiol benzoate combination with CIDR improves in-vivo embryo production as compared to conventional superovulation in bovine (Bos indicus and Bos taurus) under subtropics”. It is an interesting topic where the authors propose something new in terms of new knowledge in the area of embryo transfer.
However, in my view, the authors were unable to expose the data with sufficient clarity to approve the manuscript.
The title could be improved.
Abstract:
Insert how many animals were allocated in each group;
I couldn't find out if it was 70 cows or 90 cows?
Which breeds were crossbred cows?
The abstract was very confusing (relative to the control group), because it was difficult to know if they received FSH or not .... This has to be well specified.
Was the superovulation done in just one moment ( same time)  or in several moments?
P.7- L.41: Both groups were given SO of 11o. on the 13th day. However, elsewhere, the control also received (p.7, L48-49). He's confused.
p.7 - L 49: 90 cows? It is necessary to clarify
p.7-L50-51: phrase out of context. Add in the methodology;
What is “nondescript recipient?
Ovarian structures? What is? Specify which structures?
Again -….number of animals per group?
P.7 L52: what does super estrus follicles mean?
In the abstract: results are missing or poor described;
P.7 Substantially lower: what is it?
P7. - L55: enter the p value. The p value is missing from the table as well.
P7. 56-58: Confused. To clarify
P7 - L 62-65: improving the conclusions
P7 - L77: non descript animals? What is that?
P8- L88-89: references are missing
P.9-L114: total animals (70 or 90 cows)?
P.9-L129: on on ??? what is this?
P21 - There is a lack of incomplete legends in the figures;
Give a number to the figures
P26: what kind of animal it was (figure captions)
Table:  should be opened. There is no vertical line in the table
Table 1: symbols are missing from the variables (or % or “n”). Say what specie is ? (cow)
P10- L136: what is super estrus?
Table 1 - clarify better
No Abstract. embryos there is no mention of frozen embryos;
I could not observe the pregnancy rate of the transferred embryos. Place on the table. Will be better.
P 13- L 241- Reference: MS Khan, 2002 is not used.
Pregnancy rate of groups? where?
Table 1 legend needs to be improved (legend will go below)
Was the cows heat induced or were submitted to estrus synchronization for superovulation?

Mr. Editor,
The English language is not within my competence, but there are deficiencies in the English language.


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: GNRH OR ESTRADIOL BENZOATE COMBINATION WITH CIDR IMPROVES IN-VIVO EMBRYO PRODUCTION IN BOVINES (BOS INDICUS AND BOS TAURUS) UNDER SUBTROPICS
Review round: 1
Reviewer: 2

Output:
Basic reporting: 1.	BASIC REPORTING

The English language is unclear I recommend major editing by a native speaker

Figure 2 and 3 with very low resolution and the figure legends must be checked
Experimental design: The paper is in the journal scope but the novelty of paper is not 100%
Research question is not well established, the gap must be filled enough with more relevant information
Validity of the findings: The article is novel but the idea is studied many times before with the same combination
The benefit of the paper is not clearly stated
The statistically analysis must be provide in details by each test to provide the rationale of data
Additional comments: The plagiarism checker was adequate percentage

I again recommend improvement of the English language there were many grammatical errors in many lines The English language should be improved to understand your text.Some examples where the language could be improved include lines  36, 48, 131, 155 – the current phrasing makes comprehension difficult.

4.	Confidential notes to the editor and authors
Special comments:
Abstract: line 38 please correct the grammatical error
 Line 36: Any abbreviation must be written at first in details please check
Line 39 what do you mean by good quality corpus luteum
Line 47: authors stated (but the remaining procedure was the same…...) please clarify
Line 59-62: the conclusion is so vague and wide please adjust
Keywords: CIDR based superovulation; MOET in subtropics are not suitable words please add keywords not in the title to be more general
Introduction: first paragraph is not understood
Line 101-111 : this part need more relevant references ,,,there were many papers discussing those points
What about the main idea>>the paper hypothesis ???
Line 116: please provide references to BCS
Line 127-144: very long paragraph and filled with information
I suggest summarizing this part
Also I suggest to provide the diagram summarize the methodology and the research question to be more simple to the readers
Line 144: what about sample size ,inclusion and exclusion criteria???
Line 150-154: image must be adjusted with better resolution
Line 155: what is the ultrasound settings:::
159-166: very long paragraph rich with many grammatical error I agai suggest and English editing to this paper
Freezing and Storage of Embryos and fertility paragraphs were difficult to understand. Both showed by adjusted with many references with removing all extra spaces and correct the errors in those two paragraphs
Line 192-201: did data checked first for normality of not???
Please give the rationale for using one way ANOVA
Line 201: P value must be italic
Results
 Line 216-219: where is the table of  figure determine this result in return to estrous please clarify,,,,
Discussion
Please add more on application of MOET protocols…. With relevant new references
The discussion must start with similarity with others then ,,,the disagreement points for each item in the result section,,,, this section need to be rewritten again as its generalized with vague rationale
Conclusion ; add more in this part


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: GNRH OR ESTRADIOL BENZOATE COMBINATION WITH CIDR IMPROVES IN-VIVO EMBRYO PRODUCTION IN BOVINES (BOS INDICUS AND BOS TAURUS) UNDER SUBTROPICS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The English language used in this manuscript requires major improvement. It includes terms or expressions that are not technically correct. In general, many sections are difficult to understand. I recommend that the authors have their manuscript revised by a professional language editing service.
The introduction of the manuscript fails to demonstrate the contribution of the study to the field of knowledge. Relevant prior literature was not included. I suggest that the authors make an updated review of literature from the last five years to see all that has been done in the area where their study fits.
Captions for the figures and table are not clear. For example, the label for figure 3 represents only part of it.
Experimental design: The research question is not relevant. There was no knowledge gap being investigated and therefore the study did not contribute to filling any knowledge gap, as a number of previous studies have addressed the same topic. I suggest that the authors update their information.
The study included three experimental groups. However, one of them included twice as many animals as the other two; this can lead to errors in the statistical analysis.
The number of animals of each breed in each group was not included, even though the breed was considered as a factor in the analysis.
Validity of the findings: There is no clear contribution of this manuscript to the existing literature. I recommend that the authors revise the existing literature to update their knowledge on the field.
Additional comments: Please find some particular comments on your manuscript in the file attached. They're made to improve it.


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

Input:
Title: GNRH OR ESTRADIOL BENZOATE COMBINATION WITH CIDR IMPROVES IN-VIVO EMBRYO PRODUCTION IN BOVINES (BOS INDICUS AND BOS TAURUS) UNDER SUBTROPICS
Review round: 2
Reviewer: 1

Output:
Basic reporting: The English language is still  unclear I recommend minor editing by a native speaker
Experimental design: perfect
all suggestions are now modified
Validity of the findings: The article is novel
the idea is studied many times before with the same combination
The benefit of the paper is now clearly stated
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: GNRH OR ESTRADIOL BENZOATE COMBINATION WITH CIDR IMPROVES IN-VIVO EMBRYO PRODUCTION IN BOVINES (BOS INDICUS AND BOS TAURUS) UNDER SUBTROPICS
Review round: 2
Reviewer: 2

Output:
Basic reporting: The manuscript revised was a corrected version of the original one. However, although most of the reviewer's comments were considered, the corrections made were not sufficient to render the manuscript suitable for publication. The introduction is very long, with confusion in the objective of the study, and with no information to support it. I'm not saying that the topic addressed is not important, but it is not clearly stated in the document. In addition, there are not sufficient references to support the study. The presentation of the results is somewhat confusing, and the discussion is repetitive and not clear. The conclusions should also be revised.
One of the main flaws I found in this manuscript is the use of the English language. Although the authors said it was checked by someone who speaks English, it is still unclear and confusing and uses many terms that are not quite technically correct. The misuse of the language makes most of the manuscript hard to understand and follow. Therefore, I recommend the authors have the manuscript checked by a professional language editing service. Maybe they could first send it to check by an English-speaking colleague to choose the most appropriate technical terms.
Experimental design: It is not clear how the research from this study fills a specific knowledge gap. The writing of the material and methods section needs improvement.
Validity of the findings: It is not clear the contribution of the results to the research area. The conclusions need revision. The study did not evaluate modified superovulation protocols, but hormonal combinations that can be used before the typical superovulation protocol.
Additional comments: Even though the authors made most of the corrections indicated and checked the language use, it was not enough to make the manuscript suitable for publication. The manuscript needs major revision, including the information considered as background for the study, the aim of the study, and the relevance of the research question. The knowledge gap being investigated is not clear, nor is the contribution of the study to filling that gap. The use of the English language requires major improvement. In my opinion, it should be first revised thoroughly by the authors, including the use of the most appropriate technical terms, and then have it checked by a professional language editing service. After doing that, you could try submitting it for a new review, particularly if you consider that the information contained in your study is important.


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: DETERMINING RELEVANT TRAITS FOR SELECTING LANDRACE ACCESSIONS OF PHASEOLUS LUNATUS L. FOR INSECT RESISTANCE
Review round: 1
Reviewer: 1

Output:
Basic reporting: English language is professional and clear, even though some sentences should be checked:
L29: “even though” is used while the two accessions cited are not in the genotypes listed in the same sentence (L27 to L28).
L80 and L97 : “data were” should be replaced by “data was”

Introduction is very short and barely explains the background and the question this paper tries to answer. The information of the link between the measured traits and the resistance to insect should be stated in the introduction to explain better how these measures can answer the question. Nevertheless, to my knowledge, this is the first time the correlation between “resistance traits” listed in this paper and damage severity from herbivorous insect is assessed on Phaseolus lunatus. This statement should be placed in the introduction, to clarify the goal of the study.
Nevertheless, we can find information about the link between resistance traits and damage severity in the discussion. I suggest these paragraphs are moved in the introduction:
-	Sentence from L197 to L199.
-	Sentence from L207 to L212
-	Paragraph from L216 to L219

In general, the literature is well referenced and relevant, even though the manuscript will be clearer if the authors mention the model used in the cited papers, to better understand if the knowledge refers to beans, Fabacea, or other crops. In general also, the literature cited is old and the authors should check if newer relevant literature exists.
Here are some specific points:
L38, the Panda and Kush 2001 citation is Panda and Kush 1995 in the reference list, and Chen et al 2015 is Chen et al 2016 in the reference list.
L46, a citation should be added to the statement of beans being the second most important crop in the world
L 199, Saheb et al 2008 is Saheb et al 2018 in the reference list.
L218 Oghiakhe et al 1993 is 1992 in the reference list.

Structure of the article is conform to PeerJ standards and discipline norm.

Figure 1 and 2 would be read more easily if they had a letter to refer to the specific measure. I suggest the graph for “Number of leaves” measure is called “Figure 1 A” and “leaf area” is called “Figure 1 B”, etc. It would also facilitate the citation of these figures in the main text.
-	Figure 1 is relevant, even though I suggest the quality of the image should be improved. The bars should be clearly defined (standard deviation, standard error to the mean?)
-	Figure 2 is relevant, but the statistical groups of the photosynthetic rate and intercellular carbon are not accurate. For example, on the figure of the photosynthetic rate, genotype 9 is in group “a” while we can clearly see the mean is lower than genotype 3, which is in group “b”. The same issue is found on the figure of intercellular carbon. The statistical analysis should be double-checked. The bars should be clearly defined (standard deviation, standard error to the mean?)
-	Figure 3 is relevant but there is no label on the axis. They should state RDA axis number and the percentage of variation which is explained by each axis.
-	Table 2 would be read more easily if it was a figure. I suggest a graph format such as a histogram.
-	Table 3 would also be read more easily if it was a figure. I suggest data plots with PC1 versus PC2 as axis, and PC2 versus PC3 in another data plot, etc. The title of this figure reports 13 leaf characteristics while there are only 12.
-	In supplementary data 1, sheet “Traits” the plot names are still in Spanish
Experimental design: The authors provided an original primary research within scope of the journal.

The question is not well defined, even though it is possible to understand it after reading the manuscript. It should be clearly stated at the end of the introduction, with the knowledge gap of finding a correlation between resistance trait and damage severity on lima bean.

Investigation seems to have been performed rigorously, even if it is not stated how the 15 individual plants were selected per accession, within the 100 available individuals. If they have been selected randomly, it should be stated, and if a method of selection was applied, it should be stated too. Additionally, the authors did not state if the measures were done in a blind manner. If it is not the case, I suggest it should be mention.

Methods are described with sufficient detail in general. Nevertheless, in the statistical analyses section, L96 to L99, it would be clearer if the exact name of the analysis was provided.
The year(s) of the experiment should be added in the “site conditions and crop establishment” section.
L80 to L81, the authors state data was recorded every 15 days from 15 DAE for 3 months, while L71 they state it was at 60 DAE, and at 30, 45 and 60 DAE for insect damage L88. It is hard to understand what measures have been done every 15 days.
L72, it is not clear if the 5 plants evaluated per subplot are the same 5 plants for each trait.
L89, it is not clear if the “same 15 plants selected per plot” are the same plants between the 3 different time points, or the same 15 plants as L72 for the resistance trait measures.
Validity of the findings: Almost all underlying data have been provided. I suggest the means and standard deviation/standard error to the mean values should be provided too. Raw data of Figure 3 should be provided. The statistical analyses of Figure 2 should be double-checked.
The conclusion is not well stated. To my understanding, the authors found a positive correlation between high value in “resistance traits” and actual resistance to herbivorous insect damages, but a negative correlation between these traits and yield. This statement should appear in the conclusion or at the end of the discussion, as it is a great finding for Lima bean breeding. I suggest the author discuss more about the correlation between the traits and the redundancy analysis to understand better the answer to the question.
Because in the material and methods it is unclear if always the same 15 individual plants per accession were used to measure the different traits, it is unclear to conclude about accurate correlations between the different traits. Indeed, the variation of the values is high for some traits, especially number of leaves, leaf area, dry mass of leaves, thickness, SLA, photosynthetic rate, transpiration and WUE. It means that each individuals can differ from another, which shows that measuring different individuals is not an optimal experimental design to conclude about correlation between these traits. Nevertheless, the measures were done only on 15 individuals, in only one environment, and only on 27 accessions for which the genetic diversity has not been assessed. For yield, the number of phenotyped accessions is only 5, leading to a very uncertain correlation since the results might not be representative and repeatable. I suggest a paragraph stating about these limits, in the discussion, should be added.
Additional comments: The authors have measured several morphological and physiological traits, and yield in field on Lima bean in Mexico. They evaluate the different correlations that can be made thanks to these measures.
In general, the manuscript is very descriptive and it is hard to understand what conclusions the authors want to draw. Even though the descriptions are relevant, it is hard to understand what is the question, and how it is answered. As a summary, here are the major reviews:
-	The redundancy analysis should be discussed more to understand better the answer to the question
-	The question should be stated at the end of the introduction
-	The statistical analysis of Figure 2 should be checked
-	The limits of the approach in terms of representativity of the accessions and repeatability of the results should be stated
-	The conclusion should answer the question stated at the end of the introduction
-	The results of table 2 and table 3 should be shown in a figure format
Nevertheless, here are some additional minor revisions:
In the results section, the citations of the highest and lowest values of each measure makes the reading of the manuscript hard. In general, there is no consistency in the order in which they are cited, which is sometimes by sorting them with the value of the measure, sometimes in the sorted order from Figure 1 and Figure 2, and sometimes with no apparent structure. Additionally, the citations of the relevant genotypes in the Abstract and the Results section are often mixed up. They should be double-checked, but here are the ones I have found:
-	L29, JMC128839 is cited twice and does not exist, they should be replaced by JMC1339 and JMC1288
-	L122, JMC1271 is cited as being the highest value leaf dry mass, while it is not the case.
-	L126, JMC1325 is cited as carrying the thickest leaves, while it should be JMC1255
-	L133 to L135, the genotypes cited as having the highest and lowest photosynthetic rates don’t match the figure 2 and the raw data.
-	L137 the JMC1364 is not supposed to be cited as the highest photosynthetic rate, it should be JMC1339
-	L137, JMC1327 should be cited instead of JMC1364
-	L139 and L140, JMC1245, JMC1337 should be replaced by JMC1350 and JMC1288. JMC1336 should be replaced by JMC1339


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: DETERMINING RELEVANT TRAITS FOR SELECTING LANDRACE ACCESSIONS OF PHASEOLUS LUNATUS L. FOR INSECT RESISTANCE
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper describes interesting research on the possibility of introducing native forms of Phaseolus lunatus L. beans into cultivation and their sensitivity to damage by herbivorous insects.
The aim of this study was to select accessions that are most resistant to damage caused by defoliating insects from among 27 local accessions of lima beans (P. lunatus) by characterizing morphological, physiological and yield traits known to contribute to insect  resistance such as dry mass of leaves, leaf area, specific leaf area (SLA), leaf thickness and  hardness, and trichome density, improvement in photosynthetic capacity, and its impact on yield.
The layout of the work is correct. Divided into introduction, research methods, results, discussion and conclusions. At the end of the work, there is a references. The test results are presented in 3 tables and 3 figures. The abstract is correctly written. It contains a summary of the conducted research and results. The statistical methods were performed correctly. The conclusions correspond to the purpose of the work. The cited literature is correct.
Experimental design: However, errors were found in the work that need to be corrected
1.	There is no research hypothesis in the introduction, it should be added.
2.	In materials and methods (site conditions and crop establishment), the soil conditions and the course of the weather during the research period and the applied plant fertilization should be added.
3.	In the data collection chapter (line 77, add the method by which the SLA was marked)
4.	Research results need to be improved. They are difficult to read due to the large number of digits. I propose to include statistical indicators (f, Df, p) in the table, which will improve the transparency of the work. The authors define a higher -lower level for all examined features, which results from tables and charts (maybe it should be specified by how many% a given feature is higher or lower). In the chapter (Physiological traits) line 137 is JMC 1364 and it should be 1339. Other data of physiological traits are also inconsistent with the data in figure 2. They should be corrected
5.	The discussion of the results is not fully understandable and requires linguistic improvement
6.	The literature does not cite Mitchell and el. (line 374)
7.	In table 2 it is doubtful that the seed yield of JMC 1348 (62.0 g / plant-1) and JMC1325 (62.5 g / plant-1) belongs to 2 different homogeneous groups (a and b).
8.	In table 3 (line 3) it should be 12 and not 13.
9.	Correction is required in English by a professional translator.
Validity of the findings: The work is an original scientific research, it brings new elements to agricultural research. The proper statistical analysis of the research results deserves attention.
After detailed corrections (minor revision), the work can be published in PeerJ.
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: DETERMINING RELEVANT TRAITS FOR SELECTING LANDRACE ACCESSIONS OF PHASEOLUS LUNATUS L. FOR INSECT RESISTANCE
Review round: 1
Reviewer: 3

Output:
Basic reporting: The introduction needs more detail. I suggest that Authors should improve the description at lines 46-50  to provide more justification for the study e.g. Why were beans selected for testing?
What pests attack him?
What are the problems in growing, etc.
Experimental design: The methods are insufficiently described.
There is no description of the conditions for growing beans.
What was the soil type?
What was the soil abundance in nutrients?

Was WUE measured with the gas analyzer?

Authors should describe the scale by which leaf damage was assessed.
Validity of the findings: The description of the results does not agree with the data presented in the table 2 and figures 1 and 2. There are numerous errors in the description of the research results and the homologous groups in the fig. 2 (e.g. photosynthesis).

Besides, when describing the results, there should be numbers next to the bean accessions, the same as in the figures (in parentheses), because data analysis is very difficult.

More comments are in manuscript.
Additional comments: The manuscript is interesting and contains a lot of valuable information, but I found a lot of mistakes that disqualify this paper in current form.
The work requires checking and correcting the entire results section and Introduction as well as Material and Methods sections supplements.


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: MIR-1293 ACTS AS A TUMOR PROMOTOR IN LUNG ADENOCARCINOMA VIA TARGETING PHOSPHOGLUCOMUTASE 5
Review round: 1
Reviewer: 1

Output:
Basic reporting: In the manuscript, Chen et al elucidate that miR-1293 promotes proliferation, migration and invasion of LUAD cells via targeting PGM5, thereby suggesting its implication as potential therapeutic target for LUAD patients. They also showed that LUAD patients have elevated miR-1293 and decreased PGM5 expression with the miR-1293 expression negatively affecting patient's survival.

Overall, this is a strong comprehensive study that elucidates that miR-1293 promotes tumor in LUAD. The language is clear and easy to follow. Proper background/context has been provided where relevant. The conclusions are well supported by experimental evidences. However, I feel the quality of some of the figures need to be improved, before the manuscript is ready for publication. I have some of my other recommendations below.
Experimental design: The experiments are well executed with proper controls. The questions are logical and the methods described in sufficient details.

I have the following suggestion:
1. Some of the figures (1A-G) need to be relabeled with bigger fonts, i think the figures are screenshots of graphs prepare by the software used, all legends in the graph need to be written in bigger legible font.
2. Do the authors have an explanation for why they were not able to see a high miR-1293 expression in LUSC cells compared to normal (1H) although they were reported to be higher on patients (1B) ? Did the authors check other LUSC cell lines (recommended)?
3. For some of the blots, a lower exposure would be better to understand the difference in protein levels (example- 3F,4D, 5A PGM5)
4. For figure 6, a timeline for the xenograft experiment will be helpful.
Validity of the findings: I found all the conclusions of the authors sound and logical.
I am curious if the author's conclusion that miR-1293 acts as a tumor promotor by targeting phosphoglucomutase 5 is unique to LUAD (What about LUSC?) and hope the authors find a way to address this either in the experiment or in the discussion section. This is especially an issue since they showed its expression is high in both LUAD and LUSC patients (1A and B), but dont show the PGM5 expression in LUSC in the later experiments.
Additional comments: There are some grammatical errors in the manuscript. Please have them proofread before final submission.


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: MIR-1293 ACTS AS A TUMOR PROMOTOR IN LUNG ADENOCARCINOMA VIA TARGETING PHOSPHOGLUCOMUTASE 5
Review round: 1
Reviewer: 2

Output:
Basic reporting: In their report, Chen et. al. analyses the expression of hsa-miR-1293 in lung adenocarcinoma tumors and explore its potential functional role on proliferation, migration and invasion of cancer cell. They finally provides In vitro and In vivo evidence that hsa-miR-1293 targets PGM5 gene, which is proposed as a plausible molecular mechanism trough which exerts its anti-neoplastic roles

Overall, the manuscript conforms to Journal's standards. It is well written, with a clear syntax and professional style. Justification for the study is properly established in the background and intro. Some minor details I still detect, includes few misspellings and syntax errors along the text, which I would invite the authors to revise. Some of them can be located in lines 27, 53, 54, 248.

In general, data provided in the form of figures and supplementary data are useful and makes it easier for the reader to follow the results and findings. An exception to this is Figure 1. I understand  some of these plots have been automatically generated by the online bioinformatics resources reviewed by the authors. Still, quality of images are of low resolution and plot titles and legends are very difficult to read. This aspect might be improved. Perhaps, authors might consider distributing plots into two separated figures.
Experimental design: Methodology is properly described, in line with the research question and objectives.

For the greatest part, procedures are described with sufficient detail an providing information for further replication. However, a minor number of procedures/findings require further description or improved clarity in order to fully permit other researchers replicate authors findings

Regarding the Bioinformatics analysis section. Here, authors claim the have employed three resources (i.e., Starbase, GEPIA2 and Linkedomics), nonetheless, in the paragraph beginning at line 182 of their results, they mention that "TargetScan" and a dataset "GSE118370", were also explored. I consider, details about what these resources are (e.g., Version, study design of dataset, etc), how they were retrieved should be briefly described in methods section.

On this same aspect, results description and discussion in line 273 could be improved, given that in its current state remains somewhat ambiguous. With particular regard to the sentence "Venn diagram was used to predict the target genes of miR-1293 from three independent database" in line 187, which I fear does not exactly convey what the authors intended, which I believe is the fact that they looked at the intersection of the results from 3 different exploration strategies to find putative miRNA targets (i,e., bioinformatic prediction of seed regions, evidence of anti correlation in expression, etc). In this context, venn diagram simply serves the purpose of visual representation.

Another point of discussion regards the functional studies. H1299 cell line was used to study the regulation exerted by miR-1293 over PGM5 expression and  H1975 cell line was used instead to perform functional studies in vivo. A brief discussion of the rationale behind this decisions would add value the research.
Validity of the findings: I consider that the characterization of of miR-1293 expression alteration and its roles at suppressing proliferation, migration and invasion of LUAD cells and its anti tumorigenic potential are well established and supported by the underlying data in this study. The discussion unfolds concisely and conclusions are congruous with original research question and restricted to the observations and supporting results.
Additional comments: I commend the authors for their work which is well presented in a concise and well supported way


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: MIR-1293 ACTS AS A TUMOR PROMOTOR IN LUNG ADENOCARCINOMA VIA TARGETING PHOSPHOGLUCOMUTASE 5
Review round: 2
Reviewer: 1

Output:
Basic reporting: No commeny
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The authors have addressed all my concerns and the manuscript is ready to be published now.


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: MIR-1293 ACTS AS A TUMOR PROMOTOR IN LUNG ADENOCARCINOMA VIA TARGETING PHOSPHOGLUCOMUTASE 5
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: The authors have properly addressed my previous comments and questions.

In light of the new data presented by the authors, I observe a pair of minor details regarding the results which could be improved. I enlist them below.

Regarding the correlations between miR-1293 and somatic mutations. Is the shown p-value related to a correlation test (e.g., Pearson, Spearman)  or is it the result of a t-test. Clarifying this information in the Methods and/or Results sections would be very helpful.

Similarly, survival analysis curves produce with bioinformatic public interfaces was most likely done using a Log rank Mantel cox test or similar test. Please clarify this in Methods or Results sections
Validity of the findings: no further comment
Additional comments: No additional comments


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

Input:
Title: DNMT FAMILY INDUCES DOWN-REGULATION OF NDRG1 VIA DNA METHYLATION AND CLINICOPATHOLOGICAL SIGNIFICANCE IN GASTRIC CANCER
Review round: 1
Reviewer: 1

Output:
Basic reporting: This article is about the methylation genes in gastric cancer.  This article is trying to elucidate the roles of these genes in gastric cancer.
Experimental design: The overall design of this study is quite general. The report of the methods needs improvement.
Validity of the findings: The validity of the results is not so reliable nor supported by their data. The findings and conclusions were not well supported.
Additional comments: This article is about the methylation genes in gastric cancer.  This article is trying to elucidate the roles of these genes in gastric cancer. The overall design of this study is quite general. The report of the methods needs improvement. The validity of the results is not so reliable nor supported by their data. The findings and conclusions were not well supported.
 Thus, I suggest rejecting this paper. One main concern are that the correlation coefficient is minimal. I also suggest the author add some gastric cancer samples to validate their findings.

1.	Line 34, for the correlation, the author should report both p-value and correlation coefficient. The p=0.88 or p=0.57 for DNMT3B should not be regarded as significant.
2.	Figure 2b, please specify the meaning of “**” .
3.	In figure 3, the correlation coefficient is small to support the correlations. A p-value less than 0.05 is significant but does not guarantee correlation.
4.	Line 120-121, please specify the type of correlation, e.g., Pearson correlation.
5.	Figure 3e, delete the extra “?”
6.	Figure 3e, the slope of the line seems inconsistent with the r-value.
7.	There are also some typos and unannotated elements of figures.