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: GENOME-WIDE ANALYSIS OF CIRCULAR RNAS IN GOAT SKIN FIBROBLAST CELLS IN RESPONSE TO ORF VIRUS INFECTION
Review round: 1
Reviewer: 2

Output:
Basic reporting: This paper is the first to report the deep-sequencing analysis of goat skin fibroblasts (GSFs) infected with Orf virus (OV), including mRNA, micro-RNA and circular RNA analysis. The paper is very well-written and provides a useful insight into host-pathogen interactions. However significantly more detail is needed in the Methods and particular figure legends. The authors also need to clarify certain aspects (for example, why particular circRNAs were chosen for qRT-PCR confirmation over others) to make it easier to read. The Discussion needs to be expanded, specifically with comparison to previous Orf virus studies.

Minor alterations:
- Throughout the text, the authors should clarify whether "upregulated" actually means "significantly overexpressed in virus-infected cells". The use of vague terms such as "up" and "down" is not sufficiently clear.
- Line 115: "normlize" > normalize
- Line 186: "Due to biological functions..." > "Due to the fact that the biological functions..."
- Line 200: "an joint" > "a joint"
- Figures 2A, 4A and 5A need Y axis titles
Experimental design: - The experimental design describes three plates of infected and three non-infected (mock) plates as controls. However following RNA sequencing, all transcripts were combined (line 103). Why were all samples combined? Differential expression analysis is only possible when duplicate (or higher) samples are analysed in parallel, against control samples. This needs clarifying in the text. At the same time, it is insufficient to simply state "perl scripts were used" without including further details as to what functions those scripts performed. Finally, when reads were mapped to the reference genome (line 100) did the authors map to mRNA only (coding regions) or to non-coding as well?

- Line 121: Why was an absolute log(2) fold change threshold of 0.58 used for the miRNA analysis?

- Volcano plots (or similar) should be included for displaying the mRNA differential expression results.

- Whilst gene ontology analysis is widely used, there is not a singular standard approach. The authors need to explain in more detail how these analyses were conducted (lines 123 onwards). What dataset was used as the background? How was the data corrected?

- The legends for Figure 1, 2 and 3 need significant expansion. They should explain the figure without the reader having to refer to the main text.

- The heatmaps (Figure 2) are useful for quality control checks. Another quality control measure which should be included is a biological coefficient of variation figure, to confirm the similarities between the three virus-infected samples and disparities between these and the three mock samples. An example is Figure 2 in He et al., 2017, which is already referenced by the authors.
Validity of the findings: - No evidence is provided that the infection was successful. I would expect the number of reads mapping to the viral genome, for each infected and mock sample, to be included in the analysis (Table 2). Additionally, why is this table only included for the circRNA libraries and not the miRNA (small RNA) libraries, which according to the Methods were processed separately?

- I strongly feel that the high number of circRNAs identified should be interpreted with caution (initially described at line 162). The authors should include additional measures to avoid false positives, such as those described in He et al., 2017. For example, I would suggest only including those circRNAs which were identified in at least two of the three replicates. Given the impressive depth of coverage this should be feasible. If the authors strongly feel that this stringency is not necessary, they should explain why.

- Figures 3 and 6 should be coloured according to which circRNAs, miRNAs and mRNAs were significantly overexpressed in either virus-infected or mock samples. This would significantly aid in interpreting the data.

- Figures 4 and S1: The GO analyses should highlight which terms arose from which dataset (either infected or mock), rather than listing them in a single histogram. It should be stated explicitly in the text that very few of the KEGG pathways are significantly enriched, as indicated by the p values. Additionally, the phrase "gene_number" is unclear. Is this an absolute gene count, in which case this is incorrectly performed? These analyses should be based upon a ratio of the number of differentially expressed genes, with that particular GO/KEGG annotation, compared to a predefined background (or example, the total number of differentially expressed genes in that sample).

- Why were those particular circRNAs chosen for confirmation by qRT-PCR? This needs to be explained further in the text. Additionally, there is no evidence that the qRT-PCRs are amplifying circRNA only, and not contaminating gDNA or linear mRNA transcripts. A figure similar to Figure 2 in Shi et al., 2017 is necessary (this is already referenced by the authors).

- Whilst the authors reference two previous studies of OV transcriptomics in the Introduction (Chen et al., 2017 and Huaijie et al., 2017), these are not discussed at all in the Discussion. The current dataset should be compared to these published works.
Additional comments: This dataset looks very interesting, however as it currently stands the analysis is not stringent enough (or it needs further explanation) to allow accurate inferences to be made. Additionally, the data needs to be presented more clearly. I feel that once these aspects are altered it will prove to be of significant interest to the virology community.


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

Input:
Title: GENOME-WIDE ANALYSIS OF CIRCULAR RNAS IN GOAT SKIN FIBROBLAST CELLS IN RESPONSE TO ORF VIRUS INFECTION
Review round: 2
Reviewer: 1

Output:
Basic reporting: Well constructed manuscript revision.
Experimental design: Experimental design is adequate.
Validity of the findings: Needs further validation.
Additional comments: I mentioned in the previous review that I think they should validate the diff. expression of their novel miRNAs at least using RT-qPCR. This was not done. In general, the authors response to my suggestions (and of the other reviewer) were basically to restate what was reported in their methods section.


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: GENOME-WIDE ANALYSIS OF CIRCULAR RNAS IN GOAT SKIN FIBROBLAST CELLS IN RESPONSE TO ORF VIRUS INFECTION
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: The manuscript is greatly improved and the Figures are now clearer and easier to interpret. Most of my initial concerns have been addressed to a satisfactory level. The online title of Supplementary Table 1 (as listed on the manuscript page within peerJ) is currently incorrect, however the data within it matches the description within the manuscript text.

There are only two remaining concerns; the text should be altered to include these caveats to the conclusions:

1) The amendment at line 263 regarding false positives is inadequate. At either line 108, or within the Discussion (line 267), the authors should explicitly state how many circRNAs were identified in at least two of the three replicates. If none of the altered circRNAs were found in more than one sample, this should be clearly stated. This would aid in the reader in judging whether a circRNA is reproducibly up- or down-regulated following virus infection, or whether some of the reads were “noise”. The circRNAs which appeared in multiple samples would be of significant interest and should be listed (either as a table or within the text).

2) The qRT-PCR still does not have the essential controls. The text should be amended to state that neither mRNA nor reverse-transcriptase-free reactions were included (I suggest at line 237) and therefore the products may be formed from either linear RNA or genomic contamination. It remains possible that the splicing junctions are actually SNPs in the cellular genome. I agree this is unlikely, and the PCR product sequencing looks convincing, but that is no reason not to include controls.
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: USE OF OPEN MOBILE MAPPING TOOL TO ASSESS HUMAN MOBILITY TRACEABILITY IN RURAL OFFLINE POPULATIONS WITH CONTRASTING MALARIA DYNAMICS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article is clear and well structured.
Experimental design: The design is solid but lack of originality.
Validity of the findings: Findings are robust but not very new to readers.
Additional comments: The authors used an open mobile mapping tool, GeoODK, to survey the rural riverine Peruvian Amazon, and analyzed travel patterns of participants. My feeling is the methodology design is solid, but it is like the same technique being used again and again in different geographic regions. In other words, it would be a good working report but lacks sufficient novelty for a publication.

1. Given its offline feature, GeoODK seems to be capable of being applied to any population. It has been used in many remote areas in China, Pakistan, and Brazil. It is not surprising it fits the rural riverine population in Amazon. In this sense, this study has no difference to other studies using GeoODK for data collection. Is this worthy of reporting in a publication?

2. The authors claim that their study is the first characterization of human mobility pattern in the rural riverine Peruvian Amazon. Please note that there is some other research that used GIS and semi-structured interviews to understand the same region.

Salonen, Maria, et al. "Critical distances: comparing measures of spatial accessibility in the riverine landscapes of Peruvian Amazonia." Applied geography 32.2 (2012): 501-513.

3. The authors may add some statistical charts to contrast travel patterns in two different watersheds. There are some text about comparison, but graphs would be more intuitive.


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: USE OF OPEN MOBILE MAPPING TOOL TO ASSESS HUMAN MOBILITY TRACEABILITY IN RURAL OFFLINE POPULATIONS WITH CONTRASTING MALARIA DYNAMICS
Review round: 1
Reviewer: 2

Output:
Basic reporting: This is a well written study with clearly illustrative figures presenting a useful methodology for collecting movement data using tablet-based applications. Although this is pilot study, the authors are clear on these limitations. The study could benefit from some clarifications on the methodology and additional background on the study site.
Experimental design: In general, the research question and methods are clearly defined but there are a few points which would benefit from further description, particularly around the collection of time data and the validation of GPS data.

Lines 44- 49: Presumably at the scale of this study, the purpose of collecting movement data relates more to the where individuals are exposed to infected mosquitoes? If so, this initial introduction would benefit from an additional sentence on exposure relative to environment and local mobility patterns.

Line 58: no mobile phone coverage within this site?

Lines 59-61: The literature around effects of cloud cover on GPS accuracy is somewhat mixed; this statement should be referenced.

Lines 80-83: This would benefit from some further description of the study site, particularly in respect to land cover and available landmarks (buildings, roads, etc. if applicable).

Line 89: What time frame were the participants asked to geo-locate the trips within? I.e. immediately after returning or several weeks following the trip?

Line 102: What census data was used? Did this include any geo-referenced data (such as locations of participant households?)

Line 108: Was the accuracy of this map affected at all by the high cloud cover? Was there any attempt to ground-truth or verify the accuracy of this map and did any of the landmarks change substantially over time (such as changing river patterns relative to season or rainfall)?

Line 117: How was the movement data validated? Was there any attempt to compare reported movements with actual mapped movements?

Line 132-137: How was the data on the time of travel collected? Are these self-reported travel times and, if so, was there any attempt to assess accuracy of these times?

Lines 138: How were plausible displacement paths determined, particularly for forest movements or other activities with no identifiable roads or rivers?
Validity of the findings: The conclusions of the study are clearly stated, with the limitations of the sampling size and pilot study approach described. To improve these conclusions, further data could be included on how the reported GPS data was validated and how validation data was collected.

Lines 182-184: How did the accuracy of self-reported movements for these areas compare to other movements (such as along rivers, roads and to major cities)?

Lines 189-190: clarify what this geo-referenced data included and how it was collected
Additional comments: Two minor comments on the title and abstract:

Title: I would revise this slightly as “use of an open-source offline mobile mapping tool” to clarify the tool was used offline (rather than the populations).

Abstract: Line 27: typo, should be “GeoODK”


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: USE OF OPEN MOBILE MAPPING TOOL TO ASSESS HUMAN MOBILITY TRACEABILITY IN RURAL OFFLINE POPULATIONS WITH CONTRASTING MALARIA DYNAMICS
Review round: 1
Reviewer: 3

Output:
Basic reporting: Overall the article was well-written and succinct. I think some information could be added in a few specific places:
- Add information on GeoODK in the introduction--it's clear from the methods how it works (drawing polylines to represent travel routes) but it would be good to have some of this info in the intro. In the Methods I would also like to see a line on how researchers would find this tool to use themselves (ie. a link to a download page)
- Add information on the types of mobility that GeoODK-collected data would be most informative for--i'm thinking of the spatial/temporal axes on Fig 1 in this article: https://malariajournal.biomedcentral.com/articles/10.1186/1475-2875-11-205 (I suspect GeoODK data would be most informative on the bottom left end of the figure, for example). This is addressed to a degree in the discussion but it would be nice to see in the introduction as well.
- re: reporting of the study: Did you have any refusals? Refusal rates or non-refusal across all participants should be noted in a line in the Results.

Specific small comments:
- Lines 50 - 61: The first sentence of the paragraph starting line 58 sounds like it applies to all the mobility data referenced in 50-57, when it really only applies to the mobile phone data and GLH data, whereas lines 59-61 apply to GPS data. Please reword for clarity
- Line 86: If this is a traveler-only subset of the census group, I'd like to see some information on the overall population, to compare how the participants differed in terms of age and occupation from the population at-large.
Experimental design: I would like to see a little more detail on the polyline creation process in the Methods--how did participants record their movements, and were these cleaned up before analysis? I'm looking at Fig 1b that has a line that very neatly follows the river, and it doesn't look like a line that a participant could easily have drawn with their finger on a tablet. (perhaps they did, though--just need detail on how the actual data collection occurred)

Did you record how long did it take for people to record their movements? Did this correlate with the amount of mobility data you got with each individual?
Validity of the findings: Is there any data to validate your travel routes with (ie. travel survey data from the same individuals collected during the census)? I'm concerned that the amount of effort required to record each trip might mean that people exclude shorter trips, and I think the paper should address these sorts of recall-related biases in some way. It's not within the scope of this study to do much, but at least it would be good to note validation as an important next step in the discussion--for example, outside of forested riverine systems, researchers could compare the GeoODK-collected data with personally-collected GPS tracker data, to confirm that GeoODK collection captures a large proportion of trips away from home.
Additional comments: Generally, this was an interesting pilot study for the use of GeoODK for tracing travel routes. The main comments I had involve reporting more information--specifically, the possible refusal rates, the amount of time/effort needed for participants to record travel, and contextualizing the GeoODK data better with other types of mobility data, in terms of relevant temporal and spatial scales.


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: USE OF OPEN MOBILE MAPPING TOOL TO ASSESS HUMAN MOBILITY TRACEABILITY IN RURAL OFFLINE POPULATIONS WITH CONTRASTING MALARIA DYNAMICS
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The authors have addressed all reviewer queries and I would recommend publication.


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

Input:
Title: USE OF OPEN MOBILE MAPPING TOOL TO ASSESS HUMAN MOBILITY TRACEABILITY IN RURAL OFFLINE POPULATIONS WITH CONTRASTING MALARIA DYNAMICS
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: I'm happy with the responses to my 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: MOLECULAR MECHANISM OF POINT MUTATION-INDUCED MONOPOLAR SPINDLE 1 (MPS1/TTK) INHIBITOR RESISTANCE REVEALED BY A COMPREHENSIVE MOLECULAR MODELING STUDY
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: This is an interesting report on the molecular dynamics (MD) simulation analysis of the structure of Mps1 and four resistant mutants. To my understanding the conclusions are in general valid and they are well presented and illustrated. Some minor modifications would need to be made before it can be published.
1.	Which method used in this study to reweight the free energy map from GaMD simulation? Maclaurin series to the 10th order, cumulant expansion to the 2nd order or other? The authors should state in the method section.
2.	Generally, please use the term "inhibitor" and not "drug" due to the target of Mps1 is a very attractive potential target, but no clinically proven drugs.
3.	Please add discussion to propose how to used MD simulation results to discover new inhibitors to combat inhibitor resistance.


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: MOLECULAR MECHANISM OF POINT MUTATION-INDUCED MONOPOLAR SPINDLE 1 (MPS1/TTK) INHIBITOR RESISTANCE REVEALED BY A COMPREHENSIVE MOLECULAR MODELING STUDY
Review round: 1
Reviewer: 2

Output:
Basic reporting: In this study, Han et al. report on their findings of molecular dynamics (MD) and Gaussian accelerated MD (GAMD) simulations of Mps1/TTK wildtype and mutant versions together with the small molecule inhibitor Cpd-5.
By using informatic tools, such as MD simulations and structural analysis as well as GaMD they show that the point mutations in Mps1 induce changes in the structure of the kinase domain of Mps1, namely the P-loop and αC-helix, which they propose to possibly explain why the mutants bind less stably to Cpd-5. The major change identified was in the van der Waals interactions between Cpd-5 and the mutants compared to Mps1-WT.  The authors also identified the residues Ile-664 and Gln-683, located in essential loops of the Mps1 kinase, that contribute majorly for the differences in binding seen between the WT and the mutants to Cpd-5.
1.	BASIC REPORTING
-	The paper is in most parts well written and clear. However, in specific cases (for example in the introduction) some formulations are misleading and need clarification -> for details see comments under Point 4.
-	The overall figure quality is good. I feel however that the figures 2 and 3 are difficult to read because of the overlapping curves (and in fig 2 the curves overlap with the labelling). Maybe splitting would be a better option (or show individual plots in the supplement) The figure legends would need some improvement and a few more explanations of what is depicted.
-	The introduction and cited literature show the context in a comprehensive and nice way. I would have only a few suggestions -> for details see comments under Point 4.
-	One thing that is completely missing is the citation and mentioning of a study that basically shows similar results and in my view was followed up by the authors to produce this manuscript (experimental methods, study design and style of manuscript). “Chen Y, Yu W, Jiang C-C, Zheng J-G. Insights into Resistance Mechanisms of Inhibitors to Mps1 C604Y Mutation via a Comprehensive Molecular Modeling Study. Molecules 2018; 23. doi:10.3390/molecules23061488”. The authors should not try to ‘hide’ this fact but use it to their advantage and elaborate on why they went a step further (other mutations than C604Y) and included new findings.
Experimental design: -	The experimental design is fine. Since my expertise lies more in the biological side of small molecule inhibitor research, I can however not fully judge the exact details of the performed methods and techniques the authors use here.
Validity of the findings: -	The authors should compare their results for C604Y with the previous study I mentioned above (Chen et al., Molecules 2018). Can their results and measurements explain why C604Y is inhibited by Cpd-5 but not Reversine?
-	The authors claim in the abstract that ‘Overall, these obtained molecular mechanisms will aid rational design of novel Mps1 inhibitors to combat drug resistance.’ I would be interested if this method can really do that and I know this might be very difficult to prove but what happens for example if one uses a structure of a small molecule inhibitor which has not been tested in these mutants yet. Or at least explain in more detail how this method can be used for these predictions (for an audience like me).
Additional comments: Mps1 is the name of the yeast version of this kinase. I would actually prefer if the authors would relate to it as Mps1/TTK (at least in the title).
The authors use the word ‘systems’ when talking about the different Mps1 versions. Maybe ‘protein’ would be a better word.
Minor points:
-	The English language should be improved. Some points are confusing and the way they are phrased is wrong.
i.	Example on line 60-62: It sounds like Mps1 recruits unattached kinetochores which is not true, but: Mps1 is recruited in early mitosis to unattached kinetochores.
ii.	Example on line 71-74: Phrase is not well structured, and it is not understandable to a broader audience. I guess what the authors mean is that in cancer cells, the resistance to Mps1 inhibitors eventually occurs and this resistance is mostly due to mutations/changes in the ATP binding pocket of the Mps1 kinase domain which leads to a remarkably attenuation of the therapeutic efficiency of the Mps1 inhibitors.
iii.	Line 76: change to ‘which together form the catalytic site to ensure the transfer of a phosphate from...’ and not transformation.
iv.	On several occasions (e.g. line 186) Mps1 is written Msp1
v.	Decide on using one- or three letter code for amino acids (one letter code - e.g. I598F vs. three-letter Ile-664)
vi.	Line 240 – line 242: This first part of the sentence makes no sense and needs revision.
vii.	Line 245: include ‘is/are’ in front of ‘still limited’?
viii.	Line 262: include ‘are’ in front of ‘similar’
ix.	Line 283 – 290: this part needs a revision. I do not understand most of the results because I have the feeling words are used wrong (e.g. line 289 ‘different’ -> difference?)
x.	Line 313: what are ‘challenging’ conflicts of interest?


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: MOLECULAR MECHANISM OF POINT MUTATION-INDUCED MONOPOLAR SPINDLE 1 (MPS1/TTK) INHIBITOR RESISTANCE REVEALED BY A COMPREHENSIVE MOLECULAR MODELING STUDY
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Sufficiently addressed my previous 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: MOLECULAR MECHANISM OF POINT MUTATION-INDUCED MONOPOLAR SPINDLE 1 (MPS1/TTK) INHIBITOR RESISTANCE REVEALED BY A COMPREHENSIVE MOLECULAR MODELING STUDY
Review round: 2
Reviewer: 2

Output:
Basic reporting: All points were addressed.
Experimental design: See my initial review.
Validity of the findings: See my initial review.
Additional comments: Thank you for addressing our comments and revising your manuscript.


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

Input:
Title: PHOTOSYNTHESIS, YIELD AND RAW MATERIAL QUALITY OF SUGARCANE INJURED BY MULTIPLE PESTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript provides information on the physiological, yield, and quality of sugarcane in response to injury by two insect species exhibiting different injury types. The information fits into the broader field of knowledge. Relevant literature is appropriately referenced. The paper is fairly well written but there are needed changes to syntax, style, and grammar.
Experimental design: The experimental and treatment design needs to be explained in more detail. What year was the experiment conducted? Was the experiment replicated just once? If so, why? Field experiments typically are replicated twice to control for the role of environment in influencing any treatment differences. A RCBD design was used, but what was the blocking factor? The authors mention they used ANOVA and an LSD Test. Why? What advantages do those procedures have over others? The authors expect to see differences among treatments so why are they using a relatively liberal means separation test? This might bias their findings. Why not use a more conservative test instead (e.g., Tukey’s, SNK)? What statistical program was used? R, SAS, other? The authors seem to have measured photosynthesis from the same experimental units throughout the seasons yet there is no mention of a repeated measures design or analysis. Why not? Also, why isn’t there a statistical evaluation for interaction between sugarcane borer and spittlebug? This seems like a highly relevant and desirable question. The authors recorded CO2 exchange rates (photosynthetic rates) but make no mention of other gas exchange variables that can be measured by the LI-6400, like stomatal conductance, intercellular CO2, and transpiration rates. These values could help tease apart potential mechanisms of impairment for spittlebug.
Validity of the findings: See above.
Additional comments: Title: Herbivores do not attack plants. Do cows attack grass? No, so why is it acceptable to say that sugarcane borer attacks sugarcane? Herbivores injure or feed on plants. Change title to: “Photosynthesis, yield, and raw material quality of sugarcane injured by Diatraea saccharalis and Mahanarva fimbriolata. Change “attack” to “injury/injure, etc” throughout the article.
Line 28. Replace “most” with “more”. Include species names with authorities for sugarcane and maize at first mention.
L 29. Insert “in those countries” after “areas”.
L 33. Change “harvest” to “harvesting”.
L 35. Delete “the”.
L 37. Insert “native” before “spittlebug”.
L 38. Delete “native”.
L 42. Delete “the”.
L 44. Delete “the”.
L 45. Replace “present superior” with “result in high yields”.
L 47. Need to define “raw material quality”.
L 52. Replace “(biotic stressors) was not addressed yet” with “have not been characterized”.
L 53. Replace “on” with “of”.
L 54. Delete the phrase after “thresholds”.
L 60. Delete “pests”.
L 61. Replace “It was adopted the…” with “A randomized complete block design (RCBD) with four replications was used.”
L 66. Replace “comprised” with “was”.
L 66. What was the density of the sugarcane plants within the 2-m long rows?
L 67. What are the dimensions of the cage and what is the size of the screening? How long were the cages on the plants?
L 70. Replace “presented” with “present”.
L 77. What is meant by “leaf +1”?
L 78. Need much more information on the LI-COR 6400. Location of manufacturer (Lincoln, Nebraska, USA). Did the authors use the integrated light source or an external source (i.e., sunlight)? What was the light intensity? Was a constant CO2 reference used? If so what was the concentration? What was the flow rate?
L 83. Replace “presented” with “had”.
L 84. Replace “photosntesis” with “photosynthesis”.
L 88. Replace “harvesting” with “harvest”.
L 93. Replace “damaged” with “injured”.
L 105. Replace “15.80%” with “15.8%”.
L 106-107. Very awkward phrasing. Rewrite.
L 109. Replace “close” with “similar”.
L 109. Insert “the” after “in”.
L 111. Replace “presented borer infestation” with “were infested”.
L 112. Replace “had the photosynthetic rate analyzed” with “were analyzed for photosynthesis.”
L 113. Replace “not enough” with “of insufficient number”.
L 115. Insert “average” before “photosynthetic” and delete “average” after “rate”. Replace “on” with “in”.
L 118. Replace “performance” with “result”.
L 120. Insert “sugarcane” before “borer” and replace “presented” with “had”.
L 121. Replace “interfere” with “affect”.
L 126. Delete “the” and replace “feeding” with “injury”.
L 130. Replace “sap” with “phloem”.
Figure 1. Need “CO2” in the y-axis.
L 140. Delete both instances of “the”.
L 141. Replace “higher” with “greater”.
L 143. Insert “negatively” in the sentence before “influenced”.
L 148. Replace “into” with “in”.
Figure 2. The “-2” before “m” needs to be superscripted.
L 155. Delete the second “the”.
L 156. Replace “being that” with “and”
L 158. Replace “were” with “was”.
L 160. Replace “damages” with “injures”.
L 162. Replace “On the other hand” with “However”.
L 162. Insert “the” before “stalk”.
L 163. Delete “occurred” and replace “enough” with “sufficient”.
L 164-165. Delete “Biometric parameters impacts, such as” and begin sentence with “Diameter…”
L 165. Delete comma after “reductions” and replace “enough” with “sufficient”.
L 165-166. Awkward sentence. Rewrite.
L 170. Replace “registered” with “observed”.
L 172 and elsewhere. The “II” abbreviation is not necessary in this manuscript. Just spell out the term each time.
L 185. Replace “Usually” with “Typically” and “to” with “with”.
L 186. Delete “into”.
L 197. Replace “around” with “on”.
L 199. Delete “holistic”.


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: PHOTOSYNTHESIS, YIELD AND RAW MATERIAL QUALITY OF SUGARCANE INJURED BY MULTIPLE PESTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Authors have done a very good job of reporting their research results.
Experimental design: Trials were very well designed. Authors have really prepared a thorough treatment list to ensure that effects of caging were factored in so that treatment effects were better measured.
Validity of the findings: Results of thier finding adds to our growing knowledge to better understand how such criptic insects such as the sugarcane borer and spittlebugs affect various plant physiological processes, sugar content, and yield of sugarcane. To my knowledge, this is the first work to addres physiological responses of sugarcane to insect feeding and how these ultimatley affects yield, Such knowledge is crucial to understnd the relationship between insect feeding, pest pressure, and threshold levels, which are key to developing managment decisions.
Additional comments: comments are made directly on the manuscript.


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

Input:
Title: AETIOLOGY OF LIVESTOCK FETAL MORTALITY IN MAZANDARAN PROVINCE, IRAN
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1) The English language usage is poor. It needs to be carefully revised throughout the entire manuscript. It is often difficult to understand the authors’ point, particularly in the discussion section.
2) The figures are not relevant to the content of the article. The 3 figures only show the electrophoresis of positive and negative PCR controls and one example of a positive and a negative sample.
3) Table 2 presents, per region, the total of samples analyzed and the number of samples that were positive to one of the pathogens tested, not separated per pathogenic agent. The authors use this table to base the claim that “The fetuses of central area showed higher positive level than the other areas and it seems that this region might be more contaminated” (lines 2014-105) but this information is not relevant when 4 completely different pathogenic agents are being taken together.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The manuscript reports on the detection of T. gondii, N. caninum, B. melitensis and E. coli in aborted fetus from sheep, cattle and goat from Mazandaran province, Iran. The purpose of the study is of great interest. However, the manuscript contains too limited information to justify publication.
A few further comments:
1) The number of samples, 70 aborted fetus from sheep (57), cattle (9) and goat (4), considering the description of the work that is presented, is too small to draw other conclusions than that these pathogenic agents occur in the area studied. However, it is possible that a detailed analysis of the results obtained taking into consideration the origin of the samples at farm level, may show interesting results. For example, just to make my point clearer, the 10 T. gondii positive results in sheep from the Center region have different meanings if all came from one farm or from different farms.
2) Samples of brain tissue and abomasal content were obtained from aborted, stillborn or weak animals that died (lines 108-109). However, only results from fetus are presented. It may be interesting to present and analyze the other results even if they are all negative.
3) There are numbers between brackets in the manuscript that probably correspond to citations of bibliographic references in a format that doesn’t have correspondence in the References section.
4) The claim that the gene chosen for T gondii PCR detection has been shown to be 200- to 300-fold more sensitive than other markers (lines 138-139), if it is not a mistake, needs bibliographic support.
5) The “C” in degree Celsius symbol should not superscript.


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: AETIOLOGY OF LIVESTOCK FETAL MORTALITY IN MAZANDARAN PROVINCE, IRAN
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors describe a current topic of importance to the livestock sector and with implications in public health.

Generally, the literature references are chosen well, but do not always comply with the journal's guidelines (numbers are used in the text body while the reference list is in alphabetical order without numbering).

Raw data and figures are appropriate.

The written English should be improved throughout the manuscript. Especially in the discussion section the English is weak and partly incomprehensible.
Experimental design: The methods the authors used are sound and properly described; however, it has to be noted that for Brucella spp. differentiation improvements of the chosen PCR method (AMOS-PCR) have been described (Bricker and Halling, 1995; Ewalt and Bricker, 2002).

The interpretation of the findings from bacterial culture are not very clear:

- Which criteria were followed to determine E. coli as etiological agent of the abortion? For example, was it found in pure culture, in fetal organs, were other infectious agents excluded, check e.g. Borel et al. 2014.

- Which specific culture was done for Salmonella spp. detection? Generally, Salmonella are detected better using enrichment media, especially in heavily contaminated samples as is abortion material. If this was not the case, I would suggest to remove the discussion about Salmonella not being an important etiological agent.
Validity of the findings: The impact and novelty of this study is geographically limited to Mazandaran province.
While the aim of the study is clear, the methods valid and the results comprehensible, the conclusion should be more concise. Which immunization would the authors recommend? What are the concrete measures for improved biosecurity and why is it suggested as an alternative to immunization? Would the authors apply these measures restricted to the restricted study area?
Additional comments: Specific comments:
- Throughout the manuscript please make sure of the correct abbreviation of degree Celsius °C with capital C.

- line 83: "some of the species of the genus Brucella are pathogenic for human (Leyla et al., 2003)" Although there are species and biovars that have been discussed as less pathogenic or even apathogenic to humans, I would rather state that the genus Brucella is generally considered pathogenic for humans (=zoonotic). For further reading see e.g. WHATMORE A.M. (2009). Current understanding of the genetic diversity of Brucella, an expanding genus of zoonotic pathogens. The chosen reference seems somewhat inappropriate.

- line 99: which tests are you exactly referring to with "Wright" (SAT?) and "2ME", please specify and use references. The current version of the OIE Manual Chapter 2.1.4. from May 2016 provides a good overview over the current methods. Moreover, first time you use 2ME please spell out (2-mercaptoethanol).

- line 114: comply to reference style

- line 126: genus names "Toxoplasma" and "Neospora" in italics

- line 129: "DNA....prepared by boiling method." I would suggest to replace this by "PCRs were performed on heat-killed cell suspensions. For this purpose, a loopful of bacterial cells..."

- line 144: H2O, please use subscript.

- line 148: please replace "acted" with "included"

- lines 164-177: the PCR you describe is commonly known as AMOS-PCR. Please italicize the numbers (711) following IS (Insertion Sequence). Please be aware that this PCR has been continously improved. While your method is valid, you could include advantages of using a more updated method in the discussion, e.g. Bricker and Halling 1995) that is able to differentiate between field and two vaccine strains.

- line 187: fourteen = 14

- line 188: with "last months of gestation" do you mean the last trimester?

- lines 198-252: The discussion is written in weak English and sometimes not comprehensible at all. It needs substantial improvement.

- line 206: please replace "researches" by "studies"

- lines 250-252: regarding E. coli and Salmonella please refer to my comments in the section "2. experimental design". Regarding fungal abortion, which is known to occur only sporadically in up to 2% of abortions, it is considering the number of cases analyzed (=70) not safe to state that fungi are not important. It would be sufficient to state that no fungi were identified as etiological agents which could be due to the sporadic nature of fungal abortion.

- lines 254-263: the conclusion should be more concise. The advantages and disadvantages of vaccination should be discussed (e.g. interference with diagnostics). Which vaccines are available? Why immunization "or" biosecurity? This should be included in the general discussion. Please also refer to my comments  in the section "3. Validity of the findings".


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

Input:
Title: AETIOLOGY OF LIVESTOCK FETAL MORTALITY IN MAZANDARAN PROVINCE, IRAN
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript requires some attention to the english throughout to help with the understanding.

There is sufficient context  and relevant literature provided for the paper.

I am not so familiar with the layout of the journal but would suggest that the data could be written up as a short communication?
Experimental design: The research is well defined and the methods used are described with sufficient detail and information to replicate.
Validity of the findings: This study reports the investigation of 70 aborted foetuses collected from sheep (n=57), goats (n=4) and cattle (n=9) looking for the presence of T.gondii, N.caninum and Brucella spp as these are known to be common causes of infectious abortion in ruminant species.
The results show the presence of T. gondii DNA in around 20% of the aborted ovine foetuses suggesting that T. gondii  may be an important cause of abortion in sheep. In future studies the authors might wish to do some histopathology analysis of the tissues to look for lesions associated with T. gondii  infections to show that T. gondii is acting as a primary pathogen in this context.
There were fewer samples available for goats and cattle, although interestingly N. caninum  DNA was detected in the bovine foetal samples and this parasite is known to be an important cause of abortion in cattle. Vertical transmission of N.caninum is very common and does not always result in abortion, therefore the presence of N.caninum DNA shows that the parasite is present but does not necessarily mean it was the cause of abortion. Some further histopathology testing to look for specific lesions will give further information in this regard.
The authors might also wish to consider examining foetal serology to give additional diagnostic information.
Additional comments: The English language needs some attention


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: AETIOLOGY OF LIVESTOCK FETAL MORTALITY IN MAZANDARAN PROVINCE, IRAN
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The manuscript was significantly improved and is now clear. I have no major comments on the present version, apart from the limited amount of novelty it reports.
The work is based on 70 aborted fetuses from Mazandaran province and their origin is presented as from east (n=16), center (n=39), and west (n=15) of the province. T. gondii was found in 1 aborted fetuses from east and 12 from center, N. caninum in 1 from east and 3 from center, B. melitensis in 2 from west and E. coli in 3 from center.
Considering the information provided, only the occurrence of these pathogenic agents can be concluded.
Sentences as, for example, “Our results showed that infection with the mentioned pathogenic agents brings about considerable fetal mortality” (abstract, lines 46-48) or “The present study pinpoints the main causes of ruminant abortion in Mazandaran Province” (discussion, line 212) do not find support in the manuscript.


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

Input:
Title: A LARGE COCKROACH FROM THE MESOSAUR-BEARING KONSERVAT-LAGERSTÄTTE (MANGRULLO FORMATION), LATE PALEOZOIC OF URUGUAY
Review round: 1
Reviewer: 1

Output:
Basic reporting: - Language seems to me good, although I am not native
- There is a substantial lack of modern literature (all is recommended in the file) - to demonstrate number of families is dated at 2013, while dozens of works have been published since that time (all are recommended in the file); also the most important papers on the fossil cockroaches are not cited (all are recommeded in the attached file); not cited is also the paper by Schneider who revise the group Neorthroblattinidae, which I am sure the taxon belongs to
- Structure is OK
- OK
Experimental design: no comment
Validity of the findings: - There are some minor concerns such as deformity presence, lack of genus description and others in the attached file. But article must be written according to the recommended alternative family determination.
--- Other OK

The article is precise and really important. I am sure authors can study the recommended literature, especially Schneider 1980 and compare all known (there are in this revision) Neorthroblattinidae. Also I am sure that authors will modify conclusion (fortunately it is also a primitive group so most, but not all conclusions are valid) and prepare a paper that will be a significant contribution to the field and out of it. Nevertheless, after very negative experience of revisions in this journal (authors did not respected revision in spite of my deep trust) I insist on seeing the manuscript again before final acceptance.
Additional comments: The article is precise and really important. I am sure authors can study the recommended literature, especially Schneider 1980 and compare all known (there are in this revision) Neorthroblattinidae. Also I am sure that authors will modify conclusion (fortunately it is also a primitive group so most, but not all conclusions are valid) and prepare a paper that will be a significant contribution to the field and out of it. Nevertheless, after very negative experience of revisions in this journal (authors did not respected revision in spite of my deep trust) I insist on seeing the manuscript again before final acceptance.

In the attached file, each color field contains comments (as previously not all authors saw that 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: A LARGE COCKROACH FROM THE MESOSAUR-BEARING KONSERVAT-LAGERSTÄTTE (MANGRULLO FORMATION), LATE PALEOZOIC OF URUGUAY
Review round: 1
Reviewer: 2

Output:
Basic reporting: Much of the work is written well and information clearly stated. However, there are sections where this is not true and the paper should be revised by a native english speaker. I have provided some feedback in the attached document.

The authors have done a good job of ascertaining a reasonable phylogenetic position for the discussed fossil and thus their usage of citations is fairly thorough, with a few select cases where statements need to be cited.

The structure of the article is fine overall but needs some reorganizing. Some small sections should be swapped between the methods and results. Within the taxonomy section the diagnosis, comparisons and description sections are a bit confused and need to be largely rearranged.

Overall, the paper discusses relevant issues, although I disagree with the discussion of the age of the geological context based on this fossil.
Experimental design: The research is within the scope and aims of the journal.

The research question is well defined, relevant to the data collected, and meaningful.

The investigation seems to clearly be performed with a high ethical standard.

The methods are described well.

The technical standard by which the investigation is carried out could be improved upon. There are two main issues.

1. While the investigators have done a good job of giving some systematic context for the fossil described this needs to be improved upon. Primarily, usage of the terminology "Blattodea", "cockroach", "blattid" and lack of the usage of the terms "Stem-Dictyoptera", and "roachoid" make the paper confusing at best and deeply misleading at worst. There is a debate about the positions of the families Phyloblattidae, Archimylacridae and other Permian roachoids. This, combined with vastly different definitions of the term "Blattodea" mean that the terminology used in this paper, without clarification, could be deeply misleading to the reader. I have given extensive references and explanation in the attached text.

I will comment colloquially on the usage of Blattodea, cockroach, blattid and other names here. All three of these terms refer to different things and none of them refer to the organisms you are describing here in this paper.

crown-Blattodea - Is an order of insects containing the extant superfamilies: Blaberoidea, Corydioidea and Blattoidea. Blattoidea contains numerous families, including Blattidae, as well as the Epifamily Termitoidae (the termites). So, Blattodea contains cockroaches AND termites.

Stem-Blattodea - contain all crown-Blattodea as well as other extinct cockroaches forming ootheca and not bearing an external ovipositor.

Cockroaches - this term refers to a paraphyletic assemblage of insects within stem and crown Blattodea that retain most of the following plesiomorphic conditions of: dorso-ventrally flattened body, lateral expanded pronotum, cursorial legs.

Blattid - this is a shortening of Blattidae, a common, extant family of cockroaches.

Mantodea - is the clade of insects that are sister to Blattodea

Crown-Dictyoptera - is a clade of insects containing both Mantodea and Blattodea.

Stem-Dictyoptera - is a clade of insects containing Mantodea, Blattodea and roachoid fossil taxa bearing an external ovipostor and other plesiomorphic characters.

Roachoid - a stem-dictyoperan; an insect appearing to have the body form of a modern cockroach (dorso-laterally flattened body, cursorial legs, wide pronotum) but bearing conditions plesiomorphic to crown-Dictyoptera (e.g. external ovipositor)

These distinctions are extremely important considering the debate about the position of such taxa. See Hornig et al and Evangelista et al for a short summary of the discrepancy.

Hörnig, M.K., Haug, C., Schneider, J.W. & Haug, J.T. 2018 Evolution of reproductive strategies in Dictyopteran insects — clues from ovipositor morphology of extinct roachoids. Acta Palaeontol. Pol. 63, 1-24.

Evangelista, D.A., Djernæs, M. & Kohli, M.K. 2017 Fossil calibrations for the cockroach phylogeny (Insecta, Dictyoptera, Blattodea), comments on the use of wings for their identification, and a redescription of the oldest Blaberidae. Palaeontol. Electronica 20.3, 1-23.

Below is a list of citations following this terminology. In the next comment I will explain further:

Wang, Z., Shi, Y., Qiu, Z., Che, Y. & Lo, N. 2017 Reconstructing the phylogeny of Blattodea: Robust support for interfamilial relationships and major clades. Sci. Rep. 7, 1-8. (doi:10.1038/s41598-017-04243-1).
Legendre, F., Nel, A., Svenson, G.J., Robillard, T., Pellens, R. & Grandcolas, P. 2015 Phylogeny of Dictyoptera: Dating the origin of cockroaches, praying mantises and termites with molecular data and controlled fossil evidence. PLoS One 10, e0130127. (doi:10.1371/journal.pone.0130127).
Djernæs, M., Klass, K.D. & Eggleton, P. 2015 Identifying possible sister groups of Cryptocercidae+Isoptera: A combined molecular and morphological phylogeny of Dictyoptera. Mol. Phylogenet. Evol. 84, 284-303. (doi:10.1016/j.ympev.2014.08.019).
Ware, J.L., Litman, J., Klass, K.-D. & Spearman, L.A. 2008 Relationships among the major lineages of Dictyoptera: The effect of outgroup selection on Dictyopteran tree topology. Syst. Entomol. 33, 429-450. (doi:10.1111/j.1365-3113.2008.00424.x).
Inward, D., Beccaloni, G. & Eggleton, P. 2007 Death of an order: A comprehensive molecular phylogenetic study confirms that termites are eusocial cockroaches. Biol. Lett. 3, 331-335. (doi:10.1098/rsbl.2007.0102).
Beccaloni, G. 2018 Cockroach Species File Online. Version 5.0/5.0.  (World Wide Web electronic publication, World Wide Web electronic publication.
Beccaloni, G. & Eggleton, P. 2013 Order: Blattodea. Zootaxa 3703, 46. (doi:10.11646/zootaxa.3703.1.10).

The discrepancy here comes from the discordance between fossil researchers and researchers on extant taxa. Grimaldi & Engel 2005 mention that Blattodea is a word used for Palaeozoic “roachoid” lineages and Blattaria is the ordinal term for extant cockroaches (at the time termites were not necessarily considered to be part of Blattaria). However, Inward et al. 2006 uses Blattodea for extant cockroaches, which follows Brunner von Wattenwyl. 1882 who was the first to say that extant cockroaches were an “order” rather than a "family" of Orthoptera. Since Inward et al. 2006 was an important paper, most people since have followed and use Blattodea in the sense of Brunner von Wattenwyl. 1882 and not that discussed by Grimaldi and Engel 2005. However, many fossil cockroach workers (but not all) ignore this and use other terminologies.

My opinion is that calling roachoids “Blattodea” is not in line with the current state of the art and widens the divide between palaeoentomologists and extant-entomologists. It is confusing to those who are unaware of the historical back and forth between the usage of these names, which is why I definitely think any palaeozoic roachoids should not referred to as Blattodea. I also think they should not be called cockroaches, but you could argue that they should be. If you want to call them cockroaches i would ask that you justify it in the paper using morphological characters.

2. A more recent set of tegmina vein homologies should be used. Although, to my understanding, Lameer is an important source that is still followed today (to some degree), there have been updates to this system, in particular by Guo et al 2013. You should follow them or a number of other Dictyoptera specific publications that would be relevant:
Guo, Y., Béthoux, O., Gu, J.-j. & Ren, D. 2013 Wing venation homologies in Pennsylvanian ‘cockroachoids' (Insecta) clarified thanks to a remarkable specimen from the Pennsylvanian of Ningxia (China). J. Syst. Palaeontol. 11, 41-46. (doi:10.1080/14772019.2011.637519).

Kukalova-Peck, J. & Lawrence, J.F. 2004 Relationships among coleopteran suborders and major endoneopteran lineages: Evidence from hind wing characters. Eur. J. Entomol. 101, 195-144.

Li, X.-R., Zheng, Y.-H., Wang, C.-C. & Wang, Z.-Q. 2018 Old method not old-fashioned: parallelism between wing venation and wing-pad tracheation of cockroaches and a revision of terminology. Zoomorphology. (doi:10.1007/s00435-018-0419-6).

Brannoch, S.K., Wieland, F., Rivera, J., Klass, K.-D., Béthoux, O. & Svenson, G.J. 2017 Manual of praying mantis morphology, nomenclature, and practices (Insecta, Mantodea). ZooKeys 696, 1-100. (doi:10.3897/zookeys.696.12542).
Validity of the findings: The data appears robust, although the illustrations could be presented in higher resolution (although perhaps this is due to the PDF generation process...I did not review individual files).

The conclusions are somewhat, but not entirely, justified given the data. In the taxonomic section, justification for the establishment of the new genus is not given, and differentiation with Qilianiblatta and Qilianiblatta namurensis is not defined. The authors also do not acknowledge literature (Ross 2012) discussing reliability and conservation of venation character states in tegminized forewings, which could be highly relevant to how meaningful their results (and the results of other taxonomic works, like that describing Qilianiblatta) are.  Also, i think the revision of the age of the geoloigical setting based on this newly described fossil are not strongly justified and actually detract from the quality of the paper (see further explanation in attached doc).
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: A LARGE COCKROACH FROM THE MESOSAUR-BEARING KONSERVAT-LAGERSTÄTTE (MANGRULLO FORMATION), LATE PALEOZOIC OF URUGUAY
Review round: 2
Reviewer: 1

Output:
Basic reporting: 'no comment'
Experimental design: 'no comment'
Validity of the findings: 'no comment'
Additional comments: The paper is now after revision acceptable (after regarding the second review in attached pdf). General comments are to compare the shape of the wing (as it differs from Quilianblatta) with Neorthroblattina and possibly others. Still lacking is the calculation of forewing area, which is easily possible. Meanwhile few papers on fossil cockroaches (notice at least those published in 2017-2019 on amber to see the general knowledge of this group) were published and this as honor to other students dealing with cockroaches should be included at least in introduction. This shifts the whole field. Fortunately I see the references by Schneider were considered after first revision.


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: OUTCOMES OF HOSPITALIZATIONS WITH ATRIAL FIBRILLATION-FLUTTER ON A WEEKDAY VERSUS WEEKEND: AN ANALYSIS FROM A 2014 NATIONWIDE INPATIENT SAMPLE
Review round: 1
Reviewer: 1

Output:
Basic reporting: No concerns.
Experimental design: No concerns.
Validity of the findings: See general comments.
Additional comments: I had the pleasure of reviewing the manuscript submitted by Dr Voruganti and colleagues to PeerJ, entitled “Outcomes of patients admitted with atrial fibrillation-flutter on a weekday versus 2 weekend: an analysis from a 2014 nationwide inpatient sample.”

In this analysis, they used data from the 2014 Nationwide Inpatient Sample to assess differences in in-hospital mortality, length of stay, procedure use, and cost in patients admitted with AF on weekdays compared to weekends. They concluded that there were no significant differences in mortality or LOS, but cardioversion use and cost was lower for patients admitted on weekends.

This is an interesting topic relevant to healthcare systems given the increasing burden of AF hospitalisations, and builds on previous studies on this topic. The main strengths of this paper are the large sample size and the nationwide cohort.

Their paper would be strengthened further by:

- Speculation, if even brief, as to the possible reasons for the contrasting findings to some of the previous studies in this area
- Expansion of the introduction to build more of a background and rationale for the current study
- Provision of further details on the NIS and how it was analysed. For example, in the first few sentences of the results, it is quoted as there being 90,701 hospitalisations, yielding an national estimate of 453,505. How are these figures calculated? If scaled up from a smaller sample size, what implications does this have on the accuracy of the information?


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: OUTCOMES OF HOSPITALIZATIONS WITH ATRIAL FIBRILLATION-FLUTTER ON A WEEKDAY VERSUS WEEKEND: AN ANALYSIS FROM A 2014 NATIONWIDE INPATIENT SAMPLE
Review round: 1
Reviewer: 2

Output:
Basic reporting: •	Please structure your abstract according to author instructions with headings (Background, Methods, Results, Discussion)
•	Although your introduction identifies an appropriate gap in the literature, it would benefit from further additions. There are numerous studies that have identified differences in outcomes between weekday and weekend admissions in other cardiovascular conditions e.g. MI and it may be helpful to add in a small amount of background information concerning this. Furthermore, there are other studies in this field related to AF that you have not included e.g.:
- Comparison of weekday vs. weekend admission on inpatient mortality and total hospital charge on atrial flutter and fibrillation: a nationwide analysis
Lee, Shawn ; Lemor, Alejandro ; Gholitabar, Farid ; Gongora, Carlos A ; Dominguez, Abel Casso ; Kroner, Paul T ; Hurtado, Carolina ; Mehta, Davendra ; Castaneda, Daniel
Circulation, Nov 8, 2016, Vol.134(19)
•	I am unclear what this sentence at line 53 ‘but the results were not replicated in a national database’ is referring to. Could you please reference this, or re-phrase for improved comprehension?
•	Please state the dates in 2014 for which this analysis was conducted.
•	In your abstract, please provide values related to number of days for length of stay, instead of just a p value.
Experimental design: •	Could you please clarify how you have moved from 90,701 hospitalisations with AF as a principal diagnosis, to a ‘national estimate of 453,505’ hospitalisations. Please clarify where this number (453,505) is from.
•	In regard to mortality, you report having adjusted for patient and hospital characteristics and disease severity, yet the factors used in your adjustment model are not listed. Please list these variables.
•	Similarly, in your secondary outcomes there is no description of variables used in the multivariate model and no table of results related to this. Your results related to greater number of comorbidities does not have an associated p value – please provide. There is no description of how information concerning co-morbidity was obtained – please provide this in the methodology.
•	For cost data, there is no text related to absolute cost values. Please provide this. Please state in your methodology how cost data was obtained.
•	There is no data related to ablation, which you have stated was one of your intended outcomes.
•	It is unclear why you have not presented your multivariate adjusted model in table or figure form.
Validity of the findings: •	The paragraph in your discussion beginning with: ‘We notice a trend in improvement of outcomes in patients with AF over a period of 6 years’ is not supported by your data. You have not undertaken any statistical testing of outcomes between these datasets, and therefore this claim is not substantiated.
•	You imply in your discussion that cardioversion is a ‘life saving procedure’. Whilst you state that cardioversion is underutilised at weekends, you have stated that outcomes are not different between weekend and weekday admissions. This could also imply that cardioversion is over utilised, perhaps inappropriately, during weekdays leading to higher cost of weekday admissions. It may be that the opportunity to improve care lies in appropriate use of this procedure at all times and your discussion should refer to this as an alternative possibility.
•	In your conclusion, you introduce the concept of ‘improved anticoagulation’ during weekend AF hospitalisations, yet there is no data in your manuscript to support this. Please do not introduce new concepts in your conclusion. This data needs to be stated as an outcome, described in the methodology and have the associated results presented.
Additional comments: Whilst this is an interesting concept, there are numerous methodological gaps in the manuscript at this stage that require rectifying. Significant expansion of the methodology section is required, with appropriate reporting of intended outcomes. The results section requires much greater detail, and appropriate description and presentation of multivariate adjusted models.


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

Input:
Title: OUTCOMES OF HOSPITALIZATIONS WITH ATRIAL FIBRILLATION-FLUTTER ON A WEEKDAY VERSUS WEEKEND: AN ANALYSIS FROM A 2014 NATIONWIDE INPATIENT SAMPLE
Review round: 1
Reviewer: 3

Output:
Basic reporting: The paper is well set out and the spelling and grammar are correct. Table 3 could be more clearly formatted. Table 1 and 2 are satisfactory.
References are satisfactory,
Experimental design: My main query here is with regards to the primary and secondary outcomes of the study.
On page 4 in the methods the authors refer to the primary outcome being a composite of 5 factors: in-hospital mortality, utilisation of cardioversion/ablation procedures, length of hospital stay, time to cardioversion and total  hospitalisation charges. However in the results section on the subsequent page the authors refer to secondary outcomes of number of cardioversion procedures, interval to the procedure, length of stay and cost of hospitalisation. The final 2 factors are the same in the primary and secondary outcomes. This reviewer is confused, are these primary outcomes or secondary outcomes?

Otherwise I am also slightly confused by the first line of the results. In the abstract the authors refer to a cohort size of 453,505 hospitalisations, however in the first line of the results the authors refer to 90,701 hospitalisations? I am confused about who these 90,701 patients are? Does this mean that nearly 350,000 hospitalisations were for atrial flutter? I would recommend the authors clarify the cohorts more clearly for the reader.
Validity of the findings: This is an interesting study. The key result is that presentation on the weekend does not increase mortality, though lower rates of cardioversion are clearly more prevalent on the weekends. This study using electronic data has a large cohort and adds to the current body of literature. The data refutes the "weekend effect" and this is important when governing health policy.

With regards to table 1, presuming the p values refer to weekend vs weekday hospitalisations there are a number of differences between the baseline characteristics (gender, race, finances etc etc), which are not really elaborated on in the results. Can the authors please clarify why there are such differences?

A nice figure showing the key results from table 2 (eg cardioversion % in each group) would improve the paper. I dont feel table 3 adds very much to the paper, i would consider modifying this table into a figure (such as a flow chart or graph of events across time) or removing it.
Additional comments: Nothing further not commented on above


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

Input:
Title: OUTCOMES OF HOSPITALIZATIONS WITH ATRIAL FIBRILLATION-FLUTTER ON A WEEKDAY VERSUS WEEKEND: AN ANALYSIS FROM A 2014 NATIONWIDE INPATIENT SAMPLE
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The authors have satisfactorily responded to my comments and suggestions, but I would recommend that a few details of now the NIS is generated (as mentioned in the rebuttal) is included in the actual manuscript for readers that are not familiar with 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: OUTCOMES OF HOSPITALIZATIONS WITH ATRIAL FIBRILLATION-FLUTTER ON A WEEKDAY VERSUS WEEKEND: AN ANALYSIS FROM A 2014 NATIONWIDE INPATIENT SAMPLE
Review round: 2
Reviewer: 2

Output:
Basic reporting: Firstly, I would like to thank the authors for their extensive revision which has improved the manuscript considerably. However, there are a number of areas that still require addressing as outlined below.

•	I think it is excessive to refer to cardioversion and ablation for AF as ‘life saving procedures’. Whilst a cardioversion may be urgently indicated in the setting of acute haemodynamic instability, I do not think it is reasonable to compare this to other procedures such as the use of primary PCI for acute myocardial infarction.
•	Tables 2 and 3 would benefit from renaming to assist with comprehensibility for readers. If I am interpreting your data correctly, Table 2 refers to differences between weekend and weekday hospital admissions for AF and Table 3 reflects the multivariate model used to predict in hospital mortality for AF admissions. Please clarify this and consider renaming the tables to reflect the data shown in them.
•	In Figure 1 and Table 2 you refer to ‘time to cardioversion’. Is this time to cardioversion and ablation or just cardioversion?
•	Figure 1 adds little to the manuscript as the same data is presented in Table 2.
Experimental design: •	I see little value in the combination of cardioversion and ablation in to one outcome. These are totally different entities and whilst cardioversion may be used acutely, I cannot think of any indication for a life saving ablation for AF. The most common scenario for AF ablation is it’s use as an elective procedure and as this is much more likely to occur on weekdays, this could skew your results. It would be of much greater benefit to present cardioversion and ablation separately.
•	In your multivariate model for prediction of in hospital mortality, were any patient characteristics considered e.g. age, comorbidities such as heart failure, hypertension, prior stroke/TIA, IHD, appropriate use of OAC? You have also stated in your methods that you adjusted for ‘disease severity’. Could you please outline what this means and how this was undertaken?
•	Are you able to present the factors examined in univariate analysis?
Validity of the findings: •	I’m not sure if I am interpreting your results correctly, but the result concerning anticoagulation on weekend vs weekday admissions states that approximately 17-19% of the sample were treated with anticoagulation. This seems an extraordinarily low number, even for a random sample. Is it possible there is some data missing here concerning prescription or use of OAC from other providers?
Additional comments: Overall, the revision you have undertaken has improved the manuscript. Further methodological detail and improvements in reporting of your data would further improve this study.


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: OUTCOMES OF HOSPITALIZATIONS WITH ATRIAL FIBRILLATION-FLUTTER ON A WEEKDAY VERSUS WEEKEND: AN ANALYSIS FROM A 2014 NATIONWIDE INPATIENT SAMPLE
Review round: 2
Reviewer: 3

Output:
Basic reporting: No issues
Experimental design: No issues
Validity of the findings: No issues
Additional comments: The revision is a vastly improved manuscript.


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

Input:
Title: EXTREMELY LOW LEVELS OF CHLOROPLAST GENOME SEQUENCE VARIABILITY IN ASTELIA PUMILA (ASTELIACEAE, ASPARAGALES)
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article is well written and the methods and results are clearly presented. Figures and tables are relevant and clearly present the data and results.

ln 27. The statement that “all major clades” are represented is not informative in terms of ordinal representation. It would be more informative to note the number of Asparagales families or subfamilies that are presented and also to state and provide a citation for family or subfamily recognition e.g. APG III or APG IV. It would also be informative if the families represented in the study were indicated in Figure 2.
ln 40. Three genera are currently recognised in Asteliaceae as per Birch (2015:  doi 10.3897/phytokeys.52.4768).
ln 133-134. The wording of the statement “The asteloid clade, including Asteliaceae, is then sister to the remaining Asparagales” implies that other astelioid clade families were represented in this study, which is not the case.  To accurately reflect the taxonomic sampling of this study, the results could be stated as “The astelioid clade, represented in this study by Asteliaceae, is then sister to the remaining Asparagales.”
ln 151. Replace “variation associated to homopolymer stretches” with “variation associated with homopolymer stretches”.
Experimental design: The reasoning for the provision of the Astelia pumila chloroplast genome is detailed and the utility of that resource is established. The methods for library preparation and genome assembly are rigorous and are described in sufficient detail so as to be informative for replication of protocols.

ln 159-160. The identification of variable sites as phylogenetically informative or not, should be included in the results.
Validity of the findings: Sampling of Astelia pumila in this study was not sufficient to quantify population genetic diversity and the statement of phylogeographic findings should be modified as noted below.

ln 160. The sampling of this study, including only five individuals, is not sufficient to support genetic structuring conclusions. This statement should be removed or reworded.
ln 163-170. The discussion of how the low levels of sequence divergence documented can be interpreted in a phylogeographic context extrapolates beyond what can be supported by the sampling in this study. The five individuals sampled may or may not accurately quantify the genetic variation present in the species, which is what is required in order to support the conclusion that Astelia pumila has undergone a “post-glacial range expansion” … “out of a single ice-age refugium” (ln 186-187). This discussion is interesting but should be noted as speculative based on the sampling in the current study.
Additional comments: The study represents a significant contribution to genomic resources available for the Asparagales. The authors are commended for an interesting discussion of the evolutionary context of the features of the chloroplast genome that were documented.


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: EXTREMELY LOW LEVELS OF CHLOROPLAST GENOME SEQUENCE VARIABILITY IN ASTELIA PUMILA (ASTELIACEAE, ASPARAGALES)
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors miss the goal while trying to address an interesting story on Astelia pumila an enigmatic taxon which is mentioned in the concluding line of the section "conclusion". Here I would appreciate if another reviewer with a strong background in plant taxonomy be invited to review this manuscript to give justice to the scientific authenticity of the concerns raised by the authors.

While going through the manuscript, I expected an interesting story that could raise curiosity behind the experimental setup for sequencing 5 cp genomes of the same species on the pretext of phylogeography.

My major concerns are:
1. Are the plant species collected in different geographical regions?

2. Why the authors have to report 5 different accessions of the same species to look for sequence variability within the species in a plant specimen?

For me it is an apparent waste of time and data redundancy. I would suggest the authors to highlight on the cp DNA of A. pumila and its taxonomic position within Asparagales. The authors rather focus on some highly variable marker regions and sequence them from several populations to arrive at the intended goal. A botanist or a plant taxonomist would be in a better situation to highlight on this.

English usage: Needless to say that the authors have expertise in english. But unfortunately they have written the manuscript hastily or forgot to proofread before uploading the manuscript. they can improvise the ms during the review period.
Some of my observations are as follows:
Abstract: line 16- "via a mapping approach" ...the authors can use the term reference based assembly
Line 32 and line 40 can be synthesized into one single sentence.
Second paragraph in the Introduction section lacks appropriate reference.
Line 46- replace the word "study system" with some appropriate phrase.
Line53-56- Reframe the sentences correctly
Line 72- Expand CONC and OLD
Line 93-96 reframe the sentences with appropriate english grammar usage
Line 99-100 Please reframe the sentences in such a way that the tool web urls are placed immediately after they are mentioned in the text.
Experimental design: Research question is not well defined. I don't find any interesting knowledge gap either in the introduction nor in the discussion part.

The authors need to provide an interesting preamble to the research question and their work towards resolving it.

The authors also need to categorize the methods section into sub sections  as detailed below:

sample collection, DNA extraction and sequencing validation
Data processing
Genome annotation
Phylogeny reconstruction
etc.....

I would suggest the authors to go for SSR analysis and phylogeny based on SNP identification (using KSNP3) and identify potential RNA editing sites.
Validity of the findings: Whatever the authors have presented in the manuscript in the results section are error free. But I have a strong reservation regarding the validity of the approach to the research question by the authors.

Following are my observations:

As long as the manuscript deals with reporting of the cp DNA of A. pumila I am ok with the findings.
But as per the title of the manuscript the authors have to collect more samples, identify some interesting markers and then perform network analysis.
I would suggest the authors to follow this particular manuscript while revising their manuscript and redesigning their experiments:
"Comparative systematics and phylogeography of Quercus Section Cerris in western Eurasia: inferences from plastid and nuclear DNA variation"
https://peerj.com/articles/5793/?utm_source=summary_email_publication&utm_medium=email&utm_campaign=connection
Additional comments: I request the authors to use the cp genomes generated by them in generating a relevant and exciting manuscript. They should follow the manuscript titled "Comparative systematics and phylogeography of Quercus Section Cerris in western Eurasia: inferences from plastid and nuclear DNA variation"  in getting better ideas for developing their own paper.


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: EXTREMELY LOW LEVELS OF CHLOROPLAST GENOME SEQUENCE VARIABILITY IN ASTELIA PUMILA (ASTELIACEAE, ASPARAGALES)
Review round: 1
Reviewer: 3

Output:
Basic reporting: 1.	Introduction_ Line 39 _ need Reference.
2.	On Introduction_ Line 40. Repeated “belongs to Asteliaceae” as mentioned at the first line of Introduction.
3.	Introduction _Line 50 _After “ did not provide satisfactory results.” _need references here.
4.	Material Methods_ Line 78_ Geneious program need reference.
5.	In Material methods _ to check the junctions among LSc, SSc and IR you used Sanger Sequencing, why? As you have hundreds or thousands of these sequences reads within your genomic sequence. You just need to separate these regions (junction regions with some more nucleotides before and after) then make them as a reference, next map them to whole genomic sequences to see the error, if present, I don’t think that the only one sequence better than the whole genomic.
6.	Line 95, what was the reference genome that you used as the source of annotation chloroplast genomes?
7.	Line 104, the citation (Huson & Bryant 2006) is (2005) in the reference list.
8.	Line 106, citation (Sensu Chase, Reveal, & Fay, 2002) the year is 2009 in the reference list.
9.	Line 120 _ the end of the sentence_ after “variation was very low in A. pumila” you can cite some reference like “Wittzell, 1999; Särkinen  2013; and Salih et al. 2017”
10.	Line 154_ Laehnemann, Borkhardt & McHardy, 2015)_ the year is 2016 in the Reference list.
11.	Line 155_ after “variability was very low” cite some reference such as “Wittzell, 1999; Särkinen  2013; and Salih et al. 2017”.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: 1.	Plastome genome assembly is not easy step to get complete circular sequence using Illumina short sequences. Sometime there are many assembly errors are also happened that was reported in Scientific Reports 5: 15655. However, authors do not explain how they obtained the complete circular sequence and did not cite any other protocol.
2.	Data is not descriptive enough, though summarized. As in Introduction there is just only 4 references cited.
3.	Would be good to cite other recent papers comparing chloroplast genomes in several closely related taxa, such as “Wittzell, 1999; Särkinen  2013; and Salih et al. 2017”.
4.	What is your suggestion about choosing chloroplast marker (single gene or spacer) for the family future study? Is there any recommended region to use to get good results as whole chloroplast genome?
5.	You did the whole genomic sequences of these plants, as it should be there is whole chloroplast, nuclear, and some mitochondrial sequences. Have you assembled the whole rDNA sequences? So as to check the level of variability on ribosomal DNA.
6.	As you are the first to sequence the whole chloroplast genome of Asteliaceae, it is better to check the inventions in chloroplast genome to be as the reference for other chloroplast genome for this family in the future, there is a large inversion in chloroplast which is located within the LSC region and another one is the whole SSC inversion.


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: EVALUATION OF AAV-DJ VECTOR FOR RETINAL GENE THERAPY
Review round: 1
Reviewer: 1

Output:
Basic reporting: There are some issues in this article. It is described below.

1. In the INTRODUCTION, observation of gene delivery to retina by AAV in vitro and in vivo should be referred more because it is obscure what AAV can do in retinal gene therapy.
2. Line 93 and 163; Please correct for the words (CsCl2→CsCl2, DJ→AAV-DJ)
3. There are no results in Figure 2 H and I, but they are described in the legend.
Experimental design: Research question is unclear. The issue of retinal gene therapy with AAVs which were already performed need to be described. And, it is also obscure the reason why AAV-DJ was selected from a variety of AAVs as the subject of this study. This should be described, associated with the issue of retinal gene therapy with AAVs.
Validity of the findings: No comment
Additional comments: The article by Katada et al. evaluated the transduction efficiency of AAV-DJ vector for retina in vivo. The authors demonstrated that AAV-DJ had high transduction efficiency with all types of retinal cells and that infectious toxicity was not observed in ERG. The findings of this study are important and are expected to develop gene therapy with AAV-DJ for retinal diseases.

Major
1. The authors mentioned “the expression along the blood vessels seen in flat-mount retinas also was thought to be Mueller glia’s protrusions” in line 203 and 204. But, the evidence was not fully noted.

2. AAV-DJ has a heparin binding domain slimier to AAV-2. The cell tropism of the virus is affected by a binding ability to cell surface. However, figures 2 and 3 showed that GFP expression in Mueller cells, bipolar cells, horizontal cells, and rod photoreceptors was only found with AAV-DJ. The discussions on the function of AAV-DJ and AAV-2 or the property of these cells should be described.

3. Figure 3 only demonstrates the immunostaining imaging of retina in mice which were injected with AAV-DJ. To compare cells transduced by AAV-DJ and AAV-2, the data of AAV-2 introduction is essential (e.g. as supplementary information).

Minor
1. To define the data in the text of RESLUT, it should be represented by the number and the alphabet (e.g. Figure 1A).


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: EVALUATION OF AAV-DJ VECTOR FOR RETINAL GENE THERAPY
Review round: 1
Reviewer: 2

Output:
Basic reporting: AAV-DJ (type2/8/9 chimera) has a relatively high transduction efficiency of interest gene as a powerful tool applied for gene therapy. In this study, the authors made a successful EGFP gene transferring into retina of C57BL/6 mice. As the authors described, the results highlighted the potential usage of AAV-DJ for retinal disorders. Good news is that the neuron signal transferring pathway shown by ERG waveforms was not affected by AAV-DJ expression in retina.
These results give us a supporting data for application of AAV-DJ vector for retina-associated diseases.
Experimental design: To compare transduction efficiency between AAV-DJ and AAV-2, especially for RGC, lower amount of the vector (unsaturated dose) may be desirable in Fig. 1.
Validity of the findings: In this study, reasonable results and conclusions were acquired.
Additional comments: major comments

In Figure 2B (AAV-2), the bottom layer of ONL is intensively stained by DAPI, while there was no strong staining at the bottom of ONL in Figure 2D (AAV-DJ), rather the ONL was stained evenly by DAPI, and the bottom layer had partially fluorescence brought by AAV-DV. The authors should describe these structural difference and partial fluorescence at the bottom of ONL.

 In Figure 5, the authors measured ERG waveforms, and showed that EGFP expression did not affect the function. There was no damaged control. The authors should add another control if possible.

minor comments

All figures referred in the text should be specified like Fig. 1A, B not Figure 1.

In Figure 1 legend for D and E, the authors should describe in the legend when these confocal images were taken postinfection.

Correct the reference format in the text in line 90,
(Hitoshi, Ken-ichi & Jun-ichi, 1991) to (Niwa, Yamamura & Miyazaki, 1991). Please check other references as well.

Do not use letter “4oC” instead of “4˚C” (line 126).

In the title of Figure 2 legend, “transfection” should be changed into suitable word.

In Figure 2 legend in line 4, (C-I) should be (C-G), otherwise missing Figure 2H and Figure 2I should be added, and the authors should describe them in 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: EVALUATION OF AAV-DJ VECTOR FOR RETINAL GENE THERAPY
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The authors corrected the issues which I pointed out.
I expect that this paper will be accepted.


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: EVALUATION OF AAV-DJ VECTOR FOR RETINAL GENE THERAPY
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The revised manuscript is clearly enough for understanding smoothly the experimental design and results.
This is a prospective study that  rAAV-DJ particles could pass-through photoreceptors with intravitreal injection and apply for retina-associated diseases possibly.


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: PUTATIVELY ASEXUAL CHRYSOPHYTES HAVE MEIOTIC GENES: EVIDENCE FROM TRANSCRIPTOMIC DATA
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: Good
Validity of the findings: no comment
Additional comments: Putatively asexual chrysophytes have meiotic genes: evidence from transcriptomic data

The authors present a short report on inventory of meiosis and sex related genes from 15 representatives of chrysophytes using transcriptome data. Their findings show that chrysophytes are expressing sex genes and hence are likely sexual lineages through some obscure mechanism.

This report is a good addition in supporting the ancestral nature of sex in eukaryotes. While the goals of this manuscript are clear there some inconsistencies and sections that need clarification.

Major and minor comments are list below for consideration for the authors.

1.	The introduction clearly states there is plenty of literature indicating that chrysophytes are sexual lineages (lines 47-53), Yet the authors claim that it is putatively asexual including in the title. This is confusing. Their results also clearly demonstrate chrysophytes are sexual lineages (almost all inventoried genes have been detected). What is new here besides the lack of knowledge on the mechanism of sexual development? If the authors only analyzed lineages that are reportedly asexual they need to clarify this and give some of kind background information on those lineages.
2.	The references in this article is limited to self citation it would be nice if they can expand their references to include some recent gene inventory works in other microbial eukaryotes that used similar datasets and approach.
3.	Materials and methods – the data used in this study was from previously published work. It is not clear why the authors included methods on RNA collection and sequencing.
4.	Lines 149-151: ‘WITH’ missing or revise sentence
“Although these150 pathways have been differentially lost in various eukaryotic groups (Chi et al. 2014a; Loidl 2016), chrysophyte potentially can go down WITH both of them.”
5.	Last sentence not clear how the findings of this study could possibly help in this aspect. Please elaborate or remove
‘This finding can also be used to target￼mating attempts of different chrysophyte species in the laboratory, as these observations will offer the best evidence that the chrysophyte are truly sexual in nature.’


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: PUTATIVELY ASEXUAL CHRYSOPHYTES HAVE MEIOTIC GENES: EVIDENCE FROM TRANSCRIPTOMIC DATA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper by Kraus et al. („Putatively asexual chrysophytes have meiotic genes: evidence from transcriptomic data“) investigated the expression of nine meiosis-specific and 30 meiosis-related genes in chrysophytes - eukaryotic, single-celled organisms. They matched transcriptomic data with genes from an already published databank used for similar analyses on other protists (Cilliata and Dinoflagellata). Transcriptomic data of the 15 chrysophyte species  used were also published earlier. So this is a nice study combining existing data to investigate a specific trait. The benefit of the used method is that this trait can be quickly assessed across a range of related taxa, without difficult or impossible morphological observations.

The paper is clearly written and well structured. The introduction and background are easy to read.
The authors explain what they use as indication for sexual reproduction in crysophytes (i.e. cyst or zygote formation) which has only been observed in a few taxa.
Next to sexual reproduction, it would be interesting to understand the asexual reproduction of these organisms. Sometimes asexual reproduction also requires meiosis and meiotic genes remain functional despite being asexual (e.g. autmixis). Is it possible that the author exclude this possibility, i.e. the use of meiotic genes in asxual reproduction, in their introduction?
Experimental design: The paper generated the following data:
1) local script comparing transcriptomes against a meiotic-genes database
2) fasta sequences representing positive Blast hits, including e-values, for each strain/species

The material and method section is short and precise, though it would be helpful for reproducability of the methods, if:

a) authors could provide parameters they used for their BLAST and HMMER search. If default settings were used, it would also be nice to know.

b) which e-value threshold (similarity threshold) they used to evaluate if genes from transcriptomes were actually functional and orthologue to genes from the query database. I assume similarity of genes varied among species and were not identical to the database. E-values were provided with the fasta files in the supplementary files, but without explanation the reader is not able to understand if the e-value represents a good, mediocre or by chance hit.

c) making the local scripts available in the supplementary information would be beneficial for  the manuscript

d) to know if any paralogues were detected

The experimental design is sound and was adapted from earlier publications on similar topics.
The research question is also well-defined and is definitely relevant. Shortcomings of this methodology and dataset are openly discussed.
Methods would benefit from more transparency as mention in the section above.
Validity of the findings: Impact and novelty of this approach are limited but the general idea of this research is beneficial for  the scientific community working with protists and the field of sexual reproduction, in particular in evolutionary contexts.
As far as I could see as a reviewer the data are robust and sound, but methods are too short to judge eventually.
Discussion and Conclusions are sound and well-written.
Additional comments: No additional comments