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: ACCURATE SPATIOTEMPORAL PREDICTIONS OF DAILY STREAM TEMPERATURE FROM STATISTICAL MODELS ACCOUNTING FOR INTERACTIONS BETWEEN CLIMATE AND LANDSCAPE
Review round: 1
Reviewer: 1

Output:
Basic reporting: This paper develops models of daily mean river temperature using both linear and non-linear (gam) models with interaction terms, for 4 sub-catchments in the Columbia River. The performance of these models, in each of the catchments they were developed for, are then compared using RMSE for the training dataset, leave-one site out cross validation for training dataset and prediction to a testing dataset. The paper also explores the optimal number of sites and years required within the model and the accuracy of predicting summary metrics (e.g. monthly values) from the predicted daily river temperatures.

Generally, the paper is well written and detailed; in particular the introduction provides a nice overview. A broad range of literature is also cited. There are some interesting covariates explored, with associated reasoning. The figures and tables are well produced and the supplementary information extensive. The data sources are also provided within the methods, although some data does not appear to be available for public download currently.

I think the paper would benefit from a clearer explanation of the originality/novelty, given the number of published methods comparisons and models of river temperature. If reductions in the papers’ length were required, I would suggest that the exploration of aggregating to monthly metrics and the sensitivity analysis could be removed. I do not feel strongly about this though.

However, I do have some major concerns about the methods and specifically the statistical approach undertaken, which I will outline in the ‘experimental design’ box. I have also provided further specific comments, minor questions and references relating to this review in the ‘general comments for authors’ box.

I hope you find this review to be useful and constructive.
Experimental design: The methods section is detailed but does require some further clarification in areas:

1. My main concern regards the validity of the statistical approach. Specifically, I do not think that using interaction terms allows temporal or spatial autocorrelation to be accounted for. The assumptions of independence, required for these types of model, have still been violated. Not accounting for autocorrelation could result in covariates being retained within overly complex (over-fitted) models where there is not real statistical significance for their inclusion, as tests of statistical significance are too generous meaning type 1 errors occur more often (Isaak et al., 2014). For example, similarly to this study, a non-spatial river temperature model produced by Isaak et al., (2014) contained all significant predictor variables. However, when the same covariates were included in a spatial model only 2 out of the 5 were significant. As such, models which do not account for autocorrelation may not truly be suitable, responses could seem reasonable but may still be spurious and drawing inferences could be problematic. It is likely that this would also then have consequences for making predictions to new locations/time periods.

Residual analysis is often undertaken to establish if a model can be accepted (e.g. Laanaya et al., 2017) and if conclusions can be drawn from it (such a process is demonstrated nicely in this ‘fromthebottomoftheheap’ blog post: www.fromthebottomoftheheap.net/2014/05/09/modelling-seasonal-data-with-gam). It was good to see that temporal patterns remaining in the residuals were honestly highlighted (Figure 7) and discussed as a limitation (lines 636-637). In addition, it would be interesting to see if there were also spatial patterns remaining in the residuals (e.g. semivariograms or torgegrams), given the proximity of the sites to each other (Figure 1). Please could further details be provided to explain why the models were still accepted even with patterns in the residuals, which suggest some unsuitability?

2. Please provide further justification for why only linear and GAM models are compared. One of the objectives is to illustrate how variability commonly accounted for by hierarchical or autocorrelation statistical modelling techniques could instead be parameterised by interactions. Consequently, I would have expected comparison to a model which accounts for spatial and temporal autocorrelation. Although previous papers have shown that models which account for spatial and temporal autocorrelation perform better than models which don’t, while the magnitude of this difference varies depending on the extent of the structure in the residuals (Isaak et al., 2014).

3. Four models were produced for each catchment; linear spring, linear autumn, gam spring and gam autumn. Given that one of the benefits of gam models is being able to fit smooth terms (e.g. cubic cyclic spline for day of the year) it is unclear why the models were split into spring and autumn. Was this only to enable comparison to the linear models, where the year would have to be split to allow a linear day of the year covariate? How were the numbers of knots chosen for smooth terms and which covariates were the linear interaction terms? Further information on the model selection procedure would also be useful. Currently, it is unclear exactly how model selection was undertaken. For example were all possible model combinations compared or was it step-up step-down model selection from a full starting model? Additionally, use of an information criterion (e.g. AIC, BIC) to compare models would account for goodness of fit and the number of model parameters. This would also ensure complete comparability as linear and gam models would be ranked using the same metric (rather than R2 for linear models and deviance explained for gam). The performance of the fit of the final models (R2/deviance explained), does not appear to be provided. This would be useful and could potentially be added as rows in Table 3.

4. Inferences about the potential wider use of this approach are made. However, currently all of the model performance metrics are undertaken for the catchment that the model was developed in (so models are catchment specific) and with both the training and testing datasets covering similar spatial extents but differing time periods. It would have been interesting to explore how well the models predict to unobserved locations in distinct areas of the catchments (e.g. lower Middle Fork John Day, tributaries of the Tucannon and western tributaries of Wenatchee), particularly as issues with spatial outliers were also observed (Line 459). Wider applicability/performance could potentially have been tested for explicitly by either fitting a full model to all catchments or by testing model performance between catchments by taking a catchment model and predicting in a different catchment (e.g. Jackson et al., 2017, 2018).

5. Response shapes are categorised as ‘universal’ and ‘local’ to infer wider applicability of the models but this is not explicitly shown. A short explanation of the final models is provided, with Figure 3 illustrating an example interaction. The majority of the discussion on the model relationships is contained within the supplementary material but plots are not provided for all catchment models to allow comparison. It appears as though, for each interaction, 1 of the 4 catchments is shown for illustrative purposes.  A multi-panel plot of each individual covariate interaction in each catchment and season may be useful for demonstrating consistency in response shape and effect size.

6. It is good to see that the raw data sources are provided in the methods. I would like to see further information on why the training and testing datasets were collected from two different databases (Columbia Habitat Monitoring Programme and NorWest Regional Stream Temperature Database), rather than the testing dataset being a random sample of all of the sites/years available. For example, was this to enable testing predictions in a distinctly different time period and if so why? Although, quality control is assumed to have been undertaken by the data providers, with further visual checks undertaken prior to analysis, it could be possible that quality control and monitoring procedures (sensor/logger types and calibrations) vary between the two databases. This could introduce systematic differences between the training and testing datasets, that is an artefact of data collection rather than varying river temperatures, which may influence predictive performance. Furthermore, Table 1 provides information on the data available but what was the minimum number of data points required before a site could be used? Alternatively, were all sites used regardless of dataset length, as daily values were of interest and not summary metrics? Given the objective to model complex spatial and temporal variability in river temperature, clarification on why some sites with distinct (potentially groundwater driven) regimes were removed would also be useful. Were these sites actually monitoring temperatures in groundwater springs rather than a section of river influenced by groundwater inputs?

7. Table 2 provides a clear and concise description of the potential spatial and temporal model covariates. Temporal covariates (e.g. air temperature, discharge) were taken from single points in each catchment - was this purely down to data availability? Please provide justification of this choice. Specifically, because using the closest monitoring station or station with the most similar characteristics (if multiple stations were available) to the river temperature site may have also provided some explanation of spatial variability in climatic controls (e.g. Ta gradients/lapse rates) rather than needing to use the landscape proxies such as catchment elevation.
Validity of the findings: I am uncertain about the validity of the findings given my concerns on the methodology (details above). In brief, I have concerns that some of the model covariates may be included where a true ‘significant’ relationship is absent due to the non-independence of daily river temperature data in space and time. This is despite the exploration of the physical plausibility of the relationships in the models provided in an extensive supplementary document. It is good to see the patterns remaining in the residuals honestly described as a limitation (and illustrated in Figure 7). However, I would still argue that, as a result of assuming that observations are all independent when they are not, the models could be over-fitted, significant covariates could be spurious and parameter estimates could be driven by spatially clustered sites in the network (Isaak et al., 2014). As such, it may be inappropriate to accept and draw inferences from these models. Setting these issues aside, no models which account for autocorrelation are fitted to allow an explicit assessment into which approach performs best or to assess if the interactions would still be included as significant covariates in a model where non-independence is accounted for. Thus any suggestions that these models would outperform or have more utility than a model accounting for autocorrelation would be speculation.

There are some inferences around the wider applicability of the findings but currently each model is catchment specific and the performance metrics refer to performance at new sites and time periods within that catchment. Furthermore it seems that outlying climatic years were also removed from the testing dataset (lines 265-289), which could potentially improve model performance by ensuring predictions were not beyond the observations within the fitting period. The majority of the covariates and interactions included in the final model are contained within the supplementary material but plots do not seem to be provided for all catchment models to allow comparison of response shapes, effect sizes and importance in the models.

Information on the datasets used is stated in the methods. However, model training and testing datasets also came from two separate regional databases, potentially introducing differences as a result of different sensor/logger types and calibration procedures. This should also be acknowledged as a potential issue.
Additional comments: Here I have included specific comments for your consideration and more minor queries.

Line 82 – also difficult to upscale deterministic models

Line 88-89 – not necessarily easier to implement as they come with their own set of technical challenges and data requirements, as described by Letcher et al., (2016).

Lines 114 – please delete ‘Ashley’ for consistency with other references

Line 117 – applicable over the area they were fit for e.g. sites, catchments or regions?

Line 119-123 – given the references provided, I am not sure how the models are ‘limited in either their spatial or temporal flexibility’. The model developed by Li et al., (2014) covered 5 US states and could predict for every day of the year. The model developed by Segura et al., (2015) covered the conterminous USA and could predict monthly and seasonal river temperatures. The model developed by Jackson et al., (2018) covered Scotland and could predict for every day of the year.

Line 130 – although there are some examples where spatially and temporally (daily) continuous estimates of stream temperature could be produced (e.g. Li et al., 2014; Piccolroaz et al., 2016; Sohrabi et al., 2017; Jackson et al., 2018)

Lines 135-138 – However, by accounting for spatial and temporal correlation you would have a better model fit where all covariates are significant, rather than potentially spurious. For example, Isaak et al., (2014) provide a good overview of why autocorrelation is important and state that where autocorrelation exists, and is not accounted for, you could encounter the following problems:
1. ‘Database contains less information than the number of measurements implies’
2. ‘Tests of statistical significance are too liberal and type 1 errors occur more frequently’
3. ‘Parameter estimates may be biased or driven by spatially clustered sites’

Line 194 – why was the Chiwawa River separated out of the Wenatchee River basin?

Line 245-248 – am I correct in thinking that this was because spatially continuous predictions of climatic variables (e.g. gridded air temperature datasets) were not available? If so, a sentence stating this would be useful.

Line 274-277 – this identifies broad spatial patterns across the catchment but does not account for non-independence of sites close together. For example, Isaak et al., (2014) showed upstream catchment area to have a p value of 0.01 in a non-spatial model and 0.57 in a spatial model accounting for spatial covariance, suggesting a false detection of an effect in the non-spatial model.

Lines 284-297 – it seems like many of these interactions are used because there is not a spatially (and temporally) continuous air temperature or discharge dataset, is this correct?

Lines 510-514 – this is arguably conjecture as the ability to predict to unmonitored catchment locations (e.g. lower Middle Fork John Day, tributaries of the Tucannon and western tributaries of Wenatchee) and out with the catchments that the models were developed in (e.g. Tucannon predicting in Wenatchee) has not been tested.

Lines 527-529 – consistency in form and importance of climatic relationships across catchments does not seem to be shown. Have I missed this somewhere?

Lines 542-548 – comparing the performance of these models to models which account for spatial and temporal autocorrelation would be valuable in this respect.

Lines 558-560 – from the information provided in lines 265-268 it seems like the test dataset was compared to the training dataset to ensure that there were not outlying climatic conditions which would reduce prediction confidence. Is this correct? If so, could this be in part explaining why the models appear to have a smaller decline in precision when predicting to new years of data?

Lines 577-579 – I am not sure what is meant by this, given that the two model types in this study used the same input datasets? Please clarify.

Lines 593-595 – could this also be to do with the heterogeneity in river characteristics observed in these smaller catchments rather than inherently being to do with the size or network characteristics?

Lines 636-648 – even with improved covariate characterisation I still think the issues around spatial and temporal autocorrelation (non-independence of data) would need to be addressed.

Table 1 – Please define what you mean by effective coverage. Am I correct thinking that ‘data days by month’ is across the whole time period? A note clarifying this would be useful. I wonder if rather than ‘data days’ number of sites with days above a set threshold of days (e.g. 95%) would be more intuitive for understanding data availability.

Table 2 – Table 2 is very useful. Adding in ‘of the site’ at the end of the description in the ‘Spatial’ column for those metrics which are generated for each river temperature sites’ upstream catchment area (rather than a single whole catchment value) would further improve clarity (e.g. ‘Area’, ‘Lake’ and potentially ‘BFI’).

Table 3 – Am I correct that the grey cells in the table denote covariates included in the final model? If so, a note in the table caption would be useful to avoid potential confusion. I also wonder if something about the covariate importance in the model would be useful.

Supplementary document – this document is extensive and provides suggestions as to the physical process reasoning behind the significant interactions, which is covered to a limited extent in the manuscript itself.

Supplementary figures – these figures give an overview of the climate conditions in both training and testing datasets.

References:
Isaak, D.J., Peterson, E.E., Ver Hoef, J.M., Wenger, S.J., Falke, J.A., Torgersen, C.E., Sowder, C., Steel, A.E., Fortin, M.-J., Jordan, C.E., Ruesch, A.S., Som, N., Monestiez, P., 2014. Applications of spatial statistical network models to stream data. WIREs Water 1, 227–294.

Jackson, F. L., Fryer, R. J., Hannah, D. M., Millar, C.P., and Malcolm, I. A. (2018) A spatio-temporal statistical model of maximum daily river temperatures to inform the management of Scotland's Atlantic salmon rivers under climate change. Science of the Total Environment. 612, 1543-1558.

Jackson, F.L., Fryer, R.J., Hannah, D.M., Malcolm, I.A.,(2017) Can river temperature models be transferred between catchments? Hydrology and Earth Systems Science.  21, 4727-4745

Laanaya,F, St-Hilaire A, Gloaguen E., (2017) Water temperature modelling: comparison between the generalized additive model, logistic, residuals regression and linear regression models, Hydrological Sciences Journal, 62:7, 1078-1093.

Letcher, B.H., Hocking, D.J., O’Neill, K., Whiteley, A.R., Nislow, K.H., O’Donnell, M.J., (2016). A robust hierarchical model of daily stream temperature using air-water temperature synchronization, autocorrelation, and time lags. PeerJ 4:e1727, 3:e1971.

Li, H., Deng, X., Kim, D., Smith, E.P., (2014). Modelling Maximum Daily Temperature Using a Varying Coefficient Regression Model. Water Resources Research, 50, 3073-3087

Piccolroaz, S., Calamita, E., Majone, B., Gallice, A., Siviglia, A., and Toffolon, M. (2016) Prediction of river water temperature: a comparison between a new family of hybrid models and statistical approaches. Hydrol. Process., 30: 3901–3917.

Segura, C., Caldwell, P., Sun, G., McNulty, S., Zhang, Y., 2015. A Model to Predict Stream Water Temperature across the Conterminous USA. Hydrol. Process. 29, 2178–2195.

Sohrabi, M.M., Benjankar, R., Tonina, D., Wenger, S.J., Isaak, D.J., 2017. Estimation of Daily Stream Water Temperatures with a Bayesian Regression Approach. Hydrol. Process.


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: ACCURATE SPATIOTEMPORAL PREDICTIONS OF DAILY STREAM TEMPERATURE FROM STATISTICAL MODELS ACCOUNTING FOR INTERACTIONS BETWEEN CLIMATE AND LANDSCAPE
Review round: 1
Reviewer: 2

Output:
Basic reporting: I thought this paper was well-organized and very well done. Most of my comments pertain to points that I believe need further clarification.
The Introduction is good. The authors set up the problem and the needs well. The Methods are clear and statistically sound but I have identified some points that could be clarified. The Results and Discussion sections are comprehensive, are well-supported, and address the needs identified in the Introduction. There is a discussion of future research needs going forward as well. I did not find much to criticize with this manuscript.
I didn’t see the raw data so I wasn’t able to review or evaluate that. But the Supplemental Information explaining the physical basis for the interaction terms was very informative, probably more so than seeing the raw data.
Experimental design: The research questions were well defined. I had questions about the Methods that I think should be addressed. These are listed in the General Comments to the Author.
Validity of the findings: No comment
Additional comments: Line 157-160. The authors are presenting two different and unique approaches to stream temperature statistical modeling – the incorporation of interaction terms in the model and the use of GAMs. In these lines, they discuss the pros and cons of GAM models. They should come back to this point in the Results and Discussion. Was there any tendency for the GAMs to overfit data, as suggested here?  What were the benefits and is it recommended that these be used instead of simple linear models with interaction terms? This was addressed in the Discussion but I didn’t come away with a strong sense that I had answered these questions.
Line 221 – watershed should be plural.
Line 262-263 and lines 392-393. I’m having a little difficulty understanding how snowpack depth and stream discharge do not give you the same information and therefore result in issues of multicollinearity? After reading the Supplemental Information, I think this is clarified in that material but I would include it in the main paper too. Furthermore, why do you need Apr 1st snowpack depth (Table 3) when you have snow depth for all days? This should be explained more clearly in the paragraph from line 390-412, where you discuss the use of both Snow Depth and Apr 1st Snow Depth.
Line 308-309.  How were the spring and fall season separated on the other end of the year (in winter) with fall going into spring? Ice formation? Calendar Year?
Line 329 – is this supposed to refer to Table 1? I don’t see the relevancy of Table 1 to hypothesized effects. Is this the correct reference?
Lines 417-420. Here again, I’m having trouble understanding why the information on high tributaries versus low tributaries wasn’t captured with the Discharge term. I believe this is because you didn’t have discharge for the tribs, only the downstream end of the mainstem, but I would make this clear.
Line 460 – did you mean “better or comparable precision…”
Line 499-501 - Sensitivity analysis of years – 4+ years is very good. How does this compare to other results?
Line 587 – Please indicate how one can ensure that GAM models are not over-fitting since this is emphasized a couple of times as the negative side of GAMs – is this done through a testing dataset process or some other means?
Line 587 – “…model relationships…” or …the modeled relationship…”
Line 592 – The authors should explain why capturing a non-linear relationship is more useful in larger, more complex watersheds.
Table 2 – the descriptions for the temporal column for variables T3a and T5a appear to be reversed.
Table 2 – I’m not really understanding the variable Snow Depth and how it is different from Apr 1st snow depth. Is it collected on a particular date or was it a continuously collected throughout the season? Wouldn’t values toward the end of the season (once it starts to melt) be more important for stream temperature anyway? And why do you need Apr 1st snow depth if you have snow depth from the entire season?


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: ACCURATE SPATIOTEMPORAL PREDICTIONS OF DAILY STREAM TEMPERATURE FROM STATISTICAL MODELS ACCOUNTING FOR INTERACTIONS BETWEEN CLIMATE AND LANDSCAPE
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: I just noticed a few errors that need correction. I did not review the article extensively for corrections though.

Line 160 – “non-linear” should be “non-linearity” or “non-linearities”
Line 375 – correct “Since we contend that the RMSE test. represents the truest test of the ability of models”
Line 396 – “The mean RMSE test. for all iterations for each site count”
There are several other sentences with “RMSE test.” that need correcting.  Search for “RMSE test.” and correct the punctuation where needed.


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 IDENTIFICATION AND CHARACTERIZATION OF HEAT SHOCK PROTEIN FAMILY 70 PROVIDES INSIGHT INTO ITS DIVERGENT FUNCTIONS ON IMMUNE RESPONSE AND DEVELOPMENT OF PARALICHTHYS OLIVACEUS
Review round: 1
Reviewer: 1

Output:
Basic reporting: It is an interesting study that provided some insight into hsp70 function on immune response and early development of an commercial important (in aquaculture) flounder species (Paralichthys olivaceus). In other words, they: i) identified and characterized HSPs at the genome level,  ii) explored the evolution of HSPs and iii) its divergent functions on immune response and development stage. As major findings, and summing up: a) four genes were found under positive selection, b) hspa9, hspa12, hspa4l, hspa13 and hyou1
were induced to protect cells from stress, and c) analysis during the developmental stages indicated that hsp70s are indeed involved in the flatfish embryonic development. The paper (and respective sections) is well-structured, the methods are sound, and the conclusions supported by the obtained results. The number of Figures (#6) and References are adequate, as well as the length (number of words) of the entire ms.
The paper should be accepted after minor revisions.

Specific comments

The English language should be greatly improved.
E.g1. first line of the abstract “… and settle to a benthic in adults…”. This sentence does not make sense.
E.g.2. “…early in organismal development and are involved in cellular.”. This sentence does not make sense.
Many other examples can be found throughout the manuscript.
Experimental design: Clear. well defined.
Validity of the findings: They are statistically sound and the data quite robust.
Additional comments: NA


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 IDENTIFICATION AND CHARACTERIZATION OF HEAT SHOCK PROTEIN FAMILY 70 PROVIDES INSIGHT INTO ITS DIVERGENT FUNCTIONS ON IMMUNE RESPONSE AND DEVELOPMENT OF PARALICHTHYS OLIVACEUS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript titled “Genome-wide identification and characterization of
heat shock protein family 70 provides insight into its divergent functions on immune response and development of Paralichthys olivaceus” by Liu et al. reports the identification of 16 hsp70 genes in the genome of flatfish Paralichthys olivaceus. Characterization of these heat shock protein hsp70 s provided insights into the function of these proteins in embryonic development and in immune response of Paralichthys olivaceus. The manuscript is overall well-structured and focused. The findings are interesting and will be utilized by the scientific community. However, I have found many grammatical errors, spelling mistakes and ambiguous sentences that need to be corrected.
Authors should also discuss the findings of Qi J. et al 2014 (doi: 10.1016/j.fsi.2014.05.038) and Yong-hua Hu et al 2012 (doi.org/10.1016/j.fsi.2012.07.015) in this manuscript.
Experimental design: The experiments are well executed.
Validity of the findings: Findings are certainly interesting and will be helpful.
Additional comments: My major concerns are listed below:

Line 58: Please complete the sentence “HSC are expressed early in organismal development and are involved in cellular”.

Line 130: Replace “calculated” with “determined”.

Line 170: Lines 170-171: Please revise the subheading for the following section.

Line 204: Please provide the protein sequence alignment figure to support that hspa1b and hspa1c proteins are highly conserved.

Line 221: What does authors mean by this “hspa1a and hspa1b contained most motifs”? Please write the sentence clearly.

Line 227: Please correct “Among of them”. Remove “of”.

Line 228-229: Please rephrase the sentence “The sites were as follows: a Cys in 235 aa in hspa4l, His in 562 aa in hspa9 and His in 327aa in hspa13”, to make it clear and understandable by the future readers of the manuscript. Please take help of the other published papers for the style others opt for reporting similar results.

Line 240-241: Please revise the subheading for the following section.

Line 309: Please provide references.

Line312: Correct “thatinduce”

Line 317: “48h”, leave space between unit and time, do same wherever applicable.
Line 318 and 322: Replace “A.hydraphila with A. hydraphila” and E.tarda with E. tarda.

Manuscript is well structured, focused and experimentally sound. However, there are grammatical and spelling errors in the writing of the manuscript, Authors need to do the proofreading to avoid such errors. Manuscript also need to be revised for the quality of language used.


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 IDENTIFICATION AND CHARACTERIZATION OF HEAT SHOCK PROTEIN FAMILY 70 PROVIDES INSIGHT INTO ITS DIVERGENT FUNCTIONS ON IMMUNE RESPONSE AND DEVELOPMENT OF PARALICHTHYS OLIVACEUS
Review round: 1
Reviewer: 3

Output:
Basic reporting: In this manuscript, all the data were not verified by experiment but only data analysis. The expression of E.tar challenge and embryonic development was only identified by RNA-seq. Further, the Raw data was downloaded from NCBI (Li et al., 2018, Dev. Comp. Immunol.), and no qRT-PCRs were performed. The whole manuscript lacks novel opinion. The objective of the manuscript was ambiguous, evolution? Immunology? sex differentiation or embryonic development?

In the positive selection analysis, the authors ignored model selection. The best model should be selected or calculated before constructing phylogenetic tree, such as jModelTest or ProtTest. In this study, only six different species were used in positive selection. The number of teleost was not enough for PAML (Yang, 1997). The results of PAML about M0 vs M3, M1 vs M2 and M7 vs M8 (a) were not described.

The authors did not express clearly about the purpose of expression analysis during the developmental stages using DH & ND. The discussion about hsp70s expression in two half-sibling families is not convincing. The high expression level of hsp70 may cause low surviving rate? Further, Fig7 is not clearly arranged and easy to understand.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: No additional comments


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

Input:
Title: GENOME-WIDE IDENTIFICATION AND CHARACTERIZATION OF HEAT SHOCK PROTEIN FAMILY 70 PROVIDES INSIGHT INTO ITS DIVERGENT FUNCTIONS ON IMMUNE RESPONSE AND DEVELOPMENT OF PARALICHTHYS OLIVACEUS
Review round: 2
Reviewer: 1

Output:
Basic reporting: I am satisfied with the revision. Authors answered all my concerns and improved the manuscript wherever required.
Experimental design: The design of experiments is well plotted and well executed by the authors.
Validity of the findings: The findings are interesting and will be utilized by the scientific community. However most of the conclusions are presented based on the bioinformatic evidences only.
Additional comments: Manuscript is well structured and focused and can be considered for publication in PeerJ


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 IDENTIFICATION AND CHARACTERIZATION OF HEAT SHOCK PROTEIN FAMILY 70 PROVIDES INSIGHT INTO ITS DIVERGENT FUNCTIONS ON IMMUNE RESPONSE AND DEVELOPMENT OF PARALICHTHYS OLIVACEUS
Review round: 2
Reviewer: 2

Output:
Basic reporting: I think this revised MS should be accepted.
Experimental design: The experiments are well designed and executed.
Validity of the findings: Findings are interesting and helpful.
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: VITIS FLOWER TYPES: FROM THE WILD TO CROP PLANTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: In this manuscript (peerj-#37587), Coito and colleagues reviewed the genetics of sex determination in Vitis with male, female and hermaphrodite flowers. The authors started from famous historical phenotypic studies which established the basic theories of grapevine sex determination. Recent QTL, RNA-seq and NGS analyses were compared and integrated with early scenarios. In general, this is a careful deep review that is worth sharing with the grapevine community and the sex evolution community, however, I also have the following comments for the authors to consider in revision.
Experimental design: The literature reviewed here is complete with no bias and the historical and current investigations were incorporated very well. The writing is clear too.
Validity of the findings: The conclusions are well justified based on old and new studies.
Additional comments: Major:

1) Please write the species name correctly. Both vinifera and sylvestris are subspecies of Vitis vinifera. It should be written as Vitis vinifera subsp. vinifera and Vitis vinifera subsp. sylvestris, respectively. The author could use abbreviation after the first reference, for example, V. vinifera subsp. sylvestris (hereafter sylvestris).

2) There is very recent study using genomic sequences across tens of wild and cultivated grapevines to study the sex determination region (doi: https://doi.org/10.1101/508119), which should be included in this review because it explains some of the old theories on grapevine sex very well. The paper found important structural variations in the sex region and the phylogeny showed very interesting patterns.

Minor:

L49-53: The authors might want to update this information from current literature. The newest fossil record suggested that grapevine domesticated from their wild ancestor, the wild Eurasian grapevine (sylvestris), nearly ~8,000 years ago in the Transcaucasus (https://doi.org/10.1073/pnas.1714728114). And the only evolutionary genomic analyses suggested the human managed of wild grapevine population 22000-30000 years ago (https://doi.org/10.1073/pnas.1709257114). This is reasonable because humans should have eaten fruits before getting drunk.

L101: “and a only” should be “and an only”

L108: “XX century”: what is the XX?

L124: “has been” should be “have been”?

L134-145: The authors may want to compare these pattern with the phylogeny I mentioned above.

L326-328: This sentence is hard to follow. Please rephrase it.

L378-380: Please check whether the structural variation is in line with this observation (doi: https://doi.org/10.1101/508119).

L394: “sex locus do” should be “sex loci do” or “sex locus does”

L396: “an hermaphrodite plant” should be “a hermaphrodite plant”

L400: “indentify” should be “identify”

L408: “mendelian” should be “Mendelian”

L419: “hormone signalling” should be “hormone signaling”

Figure 2 legend: “Stout (1921 )” should be “Stout (1921)”

Figure 4 legend: “(1938 )” should be “(1938)”

Figure 5 legend: (Coito et al. 2017). According to (Oberle 1938)

Figure 5 legend: (Antcliﬀ 1980)

Figure 5 legend: “heterozygous for both SO  (So so) and SP (SP SP)” should be “heterozygous for both SO  (So so) and SP (Sp sp)”

Table 1 legend: “hermaphrodites, males and females plants” should be “hermaphrodite, male and female plants”


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: VITIS FLOWER TYPES: FROM THE WILD TO CROP PLANTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The abstract contends that the manuscript will address the hermaphrodite V. vinifera sylvestris as a wild plant or as a progenitor to domesticated grapevine, but this is barely mentioned in the body of the manuscript and certainly not as a testable hypothesis (lines 30-31).

When referring to a botanical family, the -aceae ending on the family name indicates "family", so please use "Vitaceae" and not "Vitaceae family" (lines 41, 45).

Line 42: Northern Hemisphere

At the beginning of a sentence, always spell out the genus name (line 43), such as "Vitis vinifera . . . "

Line 44: There may be only one Vitis species native to Europe, but there are many species (possibly more than 40) native to Eurasia, as Eurasia encompasses all of Asia as well as all of Europe.  Change line 44 to read ". . . in Europe".

Line 62: “14 genera” not “14 genus”.

In referring to the chromosome number, use 2n = 2x = 38 for bunch grapes (subgenus Vitis) and 2n = 2x = 40 for muscadines (subgenus Muscadinia).

The discussion of the Vitaceae should address the current and recent work on Muscadinia flower sex inheritance and mapping:
Lewter, Jennifer, Margaret L. Worthington, John R. Clark, Aruna V. Varanasi, Lacy Nelson, Christopher L. Owens, Patrick Conner, and Gunawati Gunawan. "High-density linkage maps and loci for berry color and flower sex in muscadine grape (Vitis rotundifolia)." Theoretical and Applied Genetics (2019): 1-15.

Crosses between V. vinifera and V. rotundifolia (line 66) typically are viable, in the sense that the seeds germinate and the plants grow and develop), but they are of reduced viability in the sense that the first generation hybrid vines are usually of very low fertility, with little or no set of viable seeds.  It’s inaccurate to flatly state that the hybrids are viable when this is not true; substantial qualification is needed to describe the deficiencies in the first generation hybrids.  The cross between V. vinifera and V. rotundifolia is harder to successfully conduct compared to intraspecific crosses.  The seed set is lower when crosses between these species are performed than intraspecific crosses.

The text on the polyploid origin theory (lines 69 – 80) of Muscadinia and Vitis is interesting and accurate, but it is basically not relevant to the theme of the manuscript.

Line 197:
Carbonneau (1983) may report occasional staminate flowered seedlings in crosses of perfect flowered vines.  However, Bronner (1981) reported finding 11 staminate flowered (male) vines in a self-pollinated population (total population size = 37) from Muscat Ottonel (Bronner, A. "Observation de types sexuels males dans la descendance par autofecondation de la variete Muscat Ottonel (Vitis vinifera L.)." Vitis (1981)).  Since so much of this manuscript is given to distinguishing among the models for flower type inheritance (two tightly linked loci vs one locus with three alleles), Bronner’s findings must be addressed, because these surely inform the discussion about the development and validation of the flower type models.  My reading of Bronner is that these findings indicate that there are two tightly linked loci, but in the case of Muscat Ottonel there is occasionally cross over, leading to the observation of staminate flowered vines.

Line 190:
However, the homozygous male plants are found, in direct contradiction to what is reported in the manuscript--this is found by Negi and Olmo, 1971. They created homozygous male plants and they crossed them to female plants and they got male progeny only--this is shown in their paper.  See Table 4 in Negi and Olmo, 1971, page 270.  You might not believe what is reported, but they do report that there were male flowered vines that when crossed to female vines gave only male flowered seedlings.
Experimental design: No comment.
Validity of the findings: These key conclusions or findings listed below are missing and they are major deficiencies in the state of the knowledge of the molecular genetics of grapevine flower type control:
1)	There is no sequence difference—whether SNP or structural variant, insertion, deletion, or transposition—that is shown to be causally related to flower sex differences across genotypes.  Linked markers and candidate genes are interesting, but this does not provide validation for or against a particular model and certainly does not evaluate the candidate genes.
2)	There is no gene editing, recombinant DNA, or mutagenesis validation experiment reported here to validate the candidate genes for flower type.  Did anyone use RNAi (or any other method) to turn on or off candidate genes to determine the impact on phenotype, for example?  Did anyone apply mutagenesis and then report flower type mutants in a population?
3)	The discussion of flower type mutants is totally absent.  Binova is a perfect flowered mutant of SO4, while SO4 is ordinarily male flowered.  Did anyone check the sequence of Binova to compare it with SO4?  Did anyone observe segregation of flower type in Binova progeny?  There are two rootstocks (Star 50 and Star 74) which are Binova seedlings from self-pollination, but what is the segregation of flower type in Binova self-pollinated populations (if any).  The Binova should be self-pollinated and cross pollinated, but this is unreported as far as I know.
4)	The origin of perfect flowered Muscadinia is well documented, but ignored here. For a review of grapevine flower type genetics, this must be addressed.  There are two different flower type inheritance modalities in Muscadinia.  There are probably two different loci for flower type in subgenus Muscadinia—in contrast to one locus in subgenus Vitis.  That’s very, very important for understanding the flower type pathway.
Additional comments: I suggest that the time is not right for a review of grapevine flower type.  The manuscripts cited in this review are complete and can be easily read and understood.  However, this review does not substantially improve our understanding of the current state of this particular topic.


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: VITIS FLOWER TYPES: FROM THE WILD TO CROP PLANTS
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: In this revised manuscript the authors have clearly addressed all the concerns raised. I think this is now acceptable for publication and will be of immense importance to the field. I would like to congratulate the authors on a job well done.


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: VITIS FLOWER TYPES: FROM THE WILD TO CROP PLANTS
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment.
Experimental design: No comment; this is a review manuscript.
Validity of the findings: No comment.
Additional comments: Thanks to the authors providing more information, the revised manuscript is distinctly improved from the first submission.

When referring to the species Vitis rotundifolia, this may be called V. rotundifolia (italics) or by the common name “muscadine”, but the species “V. muscadinia” is not correct.

The abstract states that three flower types can be observed: hermaphrodite in vinifera and male or female flowers in sylvestris.  This is incomplete—there are certainly pistillate flowered vinifera varieties, such as Grk and Picolit (wine grapes) and Hunisa, Chaouch, Nimrang, and Almeria (table grapes), among others.  These are completely vinifera, not sylvestris, although it is unusual—and certainly inconvenient from a horticultural perspective.  It is more complete to state that vinifera could have hermaphrodite or female flowers and sylvestris could have male or female flowers.

Line 45: Vitaceae, not Vitacea

Line 137: Use “reflexed” in place of “downright”

Lines 141-142: Explain what is meant by FFM.  I understand FM, which is a male flowered vine, heterozygous for the pistillate female flower F allele.  What is FFM?  We should expect two alleles only.

Lines 165-167: Explain why a cross between heterozygous hermaphrodites and homozygous Sp male plants should originate male and hermaphrodites in a 1:1 ratio.
We can assume that a heterozygous hermaphrodite is HF (so SP/so sp).  The homozygous male is MM (or SO SP/SO SP).  Since M is dominant to H and F, the cross of the homozygous male to any other flower class (hermaphrodite classes HH and HF, female class FF) can only produce vines that carry the dominant M (or SO SP) allele and are male flowered.  There should be no segregation observed in the offspring of homozygous males, unless there is recombination.  Address this.

Line 182: was self-pollinated

Line 205:
Explain the importance of asexual individuals—are these observed?  Does Carbonneau report them?  What are the characteristics of asexual individuals?  If there are male vines occurring in seedling populations from hermaphrodite crosses (with no male vine parent), are there asexual individuals as well?

Lines 213-214: Suggested text:
Wild vines of V. rotundifolia are dioecious, while cultivated varieties are hermaphrodite or female, similar to the flower types of cultivated vinifera and wild sylvestris.  There are two sources of hermaphroditism. . .

Line 397: The observation that chromosome 2 hosts a flower type locus in V. vinifera and in V. rotundifolia does suggest that the flower type locus may be conserved among Vitis species.  However, what evidence is there that this flower type locus is conserved among the Vitaceae?  For the flower type locus to be conserved among the Vitaceae, I would expect to see documentation of flower type locus on chromosome 2 or its equivalent in another genus (or preferably genera) in the Vitaceae, such as Cissus or Causonis.  Better to rewrite the sentence to read:
This suggests that the sex locus might be conserved among Vitis species.


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

Input:
Title: GENOMIC ANALYSES PROVIDE INSIGHTS INTO BREED-OF-ORIGIN EFFECTS FROM PUREBREDS ON THREE-WAY CROSSBRED PIGS
Review round: 1
Reviewer: 1

Output:
Basic reporting: I think the paper is interesting and worthy publishing in PeerJ. Nevertheless the style of language could be improved. Introduction section does not contain referneces of recent papers on ASE in pigs. Some sentences need to be clarified(for example abstract - line 21 -
 three kinds of crossing should be listed,lines 47-48 - I think it depends on country)
Experimental design: Methods section - not enough information is given. For example - lack of the database from which the genomes  were downloaded, lack of the details of RNA-seq library preparation. Some short cuts should be explained _ QD,MQ, FS. How was the functional enrichment analysis performed, with which dataset?
Validity of the findings: Dicussion section is lacking references to previous work on ASE in pigs and other mammals (estimation of percentage of ASE would be helpful)
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: GENOMIC ANALYSES PROVIDE INSIGHTS INTO BREED-OF-ORIGIN EFFECTS FROM PUREBREDS ON THREE-WAY CROSSBRED PIGS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is written in a clear and unambiguous English. The introduction obviously describes the background of the study, however the research hypothesis should be clearly stated. The quality of presented data is high.
Experimental design: The experiments have been conducted in conformity with ethical standards and within the aims and scope of the journal. The results of such a study may potentially be helpful to unravel the genetic background of traits important in pig industry, especially by indicating genes modulated by cis-regulatory factors. The methods described in the study allow to replicate the experiment. However, some information is missing:
-	Was the binominal test also performed for data obtained after whole genome sequencing to check for the biases in variant calling at the level of genomic DNA? Such a normalization step is a standard procedure during validation by more accurate methods and allows to reduce false positive results.
-	Did authors consider only genes in which all SNPs were found to be ASE SNPs or only a single ASE SNP was sufficient to indicate a gene as imbalanced?
-	Were the expression data adjusted for multiple testing?
Validity of the findings: My major concern regarding this manuscript is that the major scope of this study was to detect ASE by global RNA sequencing but the validation step by a more accurate method (e.g. by pyrosequencing) was not conducted. At least several genes (other than imprinted ones) should be validated to confirm subtle changes in expression of both alleles as observed after analysis of RNA seq data.
The authors concluded several times that the ASE genes detected play a major role during development of DLY pigs. In my opinion, such a conclusion is exaggerated especially that authors only detected such genes without performing any functional study. Their investigation revealed that such a phenomenon exists and is more common for genes expressed in adipose tissue (similar results were published by Schachtschneider et al., 2015 BMC Genomics. 2015;16:743) and significant cis-regulatory factors are involved but it is not possible to tell which genes are truly involved in development of the studied pigs. This is more a speculation rather than a conclusion.
Taking above into consideration the manuscript should not be published in its present form without any validation of allelic ratios for at least several genes by a more accurate method.
Additional comments: No comment


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

Input:
Title: GENOMIC ANALYSES PROVIDE INSIGHTS INTO BREED-OF-ORIGIN EFFECTS FROM PUREBREDS ON THREE-WAY CROSSBRED PIGS
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comments
Experimental design: no comments
Validity of the findings: no comments
Additional comments: no 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: GENOMIC ANALYSES PROVIDE INSIGHTS INTO BREED-OF-ORIGIN EFFECTS FROM PUREBREDS ON THREE-WAY CROSSBRED PIGS
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The authors have significantly improved their study and implemented changes in text. Although they did not meet all my suggestions, their explanation is adequate. The manuscript is now suitable for publication in PeerJ.


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: TRANSCRIPTOME SEQUENCING OF VERTICILLIUM DAHLIAE FROM A COTTON FARM REVEALS POSITIVE CORRELATION BETWEEN VIRULENCE AND TOLERANCE OF SUGAR-INDUCED HYPEROSMOSIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Generally the introduction is well written, except that I would wish to draw to the attention of the authors on the most current publications on cotton response mechanism to V. dahliae, this will help to enrich the introduction and makes it much better being the latest referenced journal is 2017, between then to date a lot has been done.
The Role of ABC promoters in enhancing resistance to V. dahliae infection (Dong et al., 2019)
Dong Q, Magwanga R, Cai X, Lu P, Nyangasi Kirungu J, Zhou Z, Wang X, Wang X, Xu Y, Hou Y, Wang K, Peng R, Ma Z, Liu F. 2019. RNA-Sequencing, Physiological and RNAi Analyses Provide Insights into the Response Mechanism of the ABC-Mediated Resistance to Verticillium dahliae Infection in Cotton. Genes 10:110. DOI: 10.3390/genes10020110.
Experimental design: Minor modifications are required in the material and methods section;
i.	Briefly describe the sample location, and why the site choice? Under the subsection  “Molecular identification of V. dahliae”
ii.	Validation of RNA-Seq Data by qRT-PCR: the authors has stated that “was used to determine the expression level of the selected genes and the SYBR Green Real-Time PCR Master Mix” provide a brief explanation on which criterion was adopted in the selection of the genes used in RT-qPCR validation”
Validity of the findings: The results are well described and supported with relevant literature citations, though few mistakes need to be corrected by the authors before submitting their final version
i.	Line 226 Change “ gene otology” to “gene ontology”
ii.	Line 239: a numerical term cannot begin the sentence, “All unigenes on the transport were screened from the DEGs data set. 169 (9% of the total…”
iii.	Gene full name description should not be italicized unless the abbreviation form is given. Line 307 to 310 and line 314 to 317 in the description of the unigenes
Additional comments: The work is very interesting and will appeal to the wider audience in cotton science. The research problem is well laid out and the methods used are appropriate.


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: TRANSCRIPTOME SEQUENCING OF VERTICILLIUM DAHLIAE FROM A COTTON FARM REVEALS POSITIVE CORRELATION BETWEEN VIRULENCE AND TOLERANCE OF SUGAR-INDUCED HYPEROSMOSIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The standard of English for most of the report is good and forms a clear narrative.

In the abstract delete the word "apparent" in line 18. On line 25 I suggest "associated with" rather than "responsible for".
Experimental design: The methods for DNA extraction, sequencing, generation of nit mutants, and pathogenicity assay all seem good and conform with best practice.
Some steps such as cloning ITS products for before sequencing and validation of RNA-seq data by qRT-PCR are excellent steps that are often missing from lesser manuscripts.

I have no comment on the transcriptomics
Validity of the findings: I analysed the attached data file of ITS sequences. There are some problems with the DNA sequences and their analysis:

SHZ-17 is not Verticillium but rather Neocosmospora rubicola (See locus2 tree)

SHZ-12 is not Verticillium but rather an Alternaria species (See locus3 tree)

This makes me very concerned for the analysis of Figure 1. I don’t see how such a tree could be calculated from this sequence data. I have attached my own tree with a very quick analysis as tree.pdf it is rather different.

Looking at the raw sequence data it appears that nearly all the variation is at the ends of the sequence. This strongly suggests that the ends are messy low-quality sequence and should be removed or validated against raw chromatogram data. (see sequence picture). Were ITS primers or the plasmid primers used to sequence it insert?
The sequence data and its analysis needs to be greatly improved.

I have no comment on the transcriptomics
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: TRANSCRIPTOME SEQUENCING OF VERTICILLIUM DAHLIAE FROM A COTTON FARM REVEALS POSITIVE CORRELATION BETWEEN VIRULENCE AND TOLERANCE OF SUGAR-INDUCED HYPEROSMOSIS
Review round: 2
Reviewer: 1

Output:
Basic reporting: good
Experimental design: good
Validity of the findings: good
Additional comments: accept


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: TRANSCRIPTOME SEQUENCING OF VERTICILLIUM DAHLIAE FROM A COTTON FARM REVEALS POSITIVE CORRELATION BETWEEN VIRULENCE AND TOLERANCE OF SUGAR-INDUCED HYPEROSMOSIS
Review round: 2
Reviewer: 2

Output:
Basic reporting: .
Experimental design: .
Validity of the findings: .
Additional comments: I thank the authors for their revisions and response to the review.
However in the current dataset the DNA sequences of
SHZ-12 matches an Alternaria species and
SHZ-17 matches a Neocosmospora species
This can be verified by analysing the sequences at https://blast.ncbi.nlm.nih.gov

I acknowledge the authors response showing the gel photos indicating bands consistent with Verticillium dahliae, so perhaps there was a mix up with these sequences and other isolates.

In this case SHZ-17 and SHZ-12 should be re-sequenced.


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: LONG-TERM PATIENT OBSERVATION AFTER CONSERVATIVE TREATMENT OF CARPAL TUNNEL SYNDROME: A SUMMARY OF TWO RANDOMISED CONTROLLED TRIALS
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: #39930
Long-term patients observation after conservative treatment of carpal tunnel syndrome: a summary of two randomised controlled trials

Overall, this is a manuscript for evaluating the outcomes changes six months after manual therapy based only on the neurodynamic techniques treatment of CTS patients. The authors performed an observational study and concluded that the use of manual therapy based on neurodynamic techniques maintains the beneficial effects 6 months after therapy in CTS patients.

The topic is quite interesting and clinical important that can significantly improve the patients’ health and influence economic and social costs. However, this manuscript is not well written and several issues need to be addressed before the article is suitable for publication.

The main issues of this manuscript includes:

1. In the Results, your most important issue is that the table didn’t include (95% CI). Another issue is that real and accurate data (numbers and p values) should be reported.

2. Follow-up 6 months means long-term? Please find some references support your opinion.

3. The discussion is too prolix. I suggest that your write paragraph 1 like this:

The present study identified that both groups were significant differences in pain and MS at follow-up 6 months. The assessment of subjective symptoms of group B showed significantly different at follow-up 6 months. However, comparable outcomes of sensory conduction velocity, motor conduction velocity, motor latency and assessment of cunction were disclosed between both groups.

The detail issues are as follows:

Line 147: This work... This study...

Line 195: Please provide detailed laboratory testing gear.

Line 234-236, 239-241: Please write real and accurate data (numbers and p values) even the results not significant difference.

Line 238: ... pain reduction was 0.34 (95% CI, 0.09–0.39) and 0.34 (95% CI, 0.18–0.51) ... ... pain reduction was 0.34 (95% CI, 0.09 - 0.39) and 0.34 (95% CI, 0.18 - 0.51) ... Please check full-text and modify them.

Line 246: ... the strength of the pinch and cylindrical grip tests improved by 0.53 kg (95% CI, 0.26–0.81) and 1.1 kg (95% CI, 0.39–1.84), respectively.  ... ...the strength of the cylindrical and pinch grip tests improved by 1.1 kg (95% CI, 0.39–1.84) and 0.53 kg (95% CI, 0.26–0.81), respectively...

Lines 253: ... (in all cases p>0.05) ... ... (in all cases P > 0.05) ... Please check full-text and modify them.

Lines 380-384: the style of references 1, 2, 3, 8 are different. Please modify them.

Table 1: ... Group A (n=46), Group B (n=61), 6months, p-value, Age(year), Body mass (kg), Height (cm), BMI (kg/m2) ... ... Group A (n = 46), Group B (n = 61), 6 months, P- value, Age (SD) years, Body mass (SD) kg, Height (SD) cm, BMI (SD) kg/m2...

Table 2: ... Group A , Group B, 6months, p-value, SCV(m/s), MCV(m/s), MT(t(ms)), NPRS (0-10), BCTQ-SSS, BCTQ-FSS, MS CG(kg), MS PG(kg) ... ... Group A (n = 46), Group B (n = 61), 6 months, P- value, SCV (SD) m/s, MCV (SD) m/s, MT (SD) t(ms), NPRS (SD) (0-10), BCTQ-SSS (SD), BCTQ-FSS (SD), MS CG (SD) kg, MS PG (SD) kg...


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: LONG-TERM PATIENT OBSERVATION AFTER CONSERVATIVE TREATMENT OF CARPAL TUNNEL SYNDROME: A SUMMARY OF TWO RANDOMISED CONTROLLED TRIALS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Literature references are old;
In the table, what does mean of the content in the bracket?
Experimental design: no comment
Validity of the findings: it's better to also compare the results in the sham group
Additional comments: The authors have extensively evaluate the long-term (six months) effects of neurodynamic techniques in the conservative treatment of CTS patients.The study could benefit from additional controls such as
the results change in the sham group.
Criticisms:
1) Literature references are old;
2) In the table, what does mean of the content in the bracket?
3) it's better to also compare the results change in the sham group.


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: LONG-TERM PATIENT OBSERVATION AFTER CONSERVATIVE TREATMENT OF CARPAL TUNNEL SYNDROME: A SUMMARY OF TWO RANDOMISED CONTROLLED TRIALS
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Lines 181-182: ... values (<50 m/s) ...change to ... values (< 50 m/s) ... ;  ...latency (>4t(ms)) ...change to ....latency (> 4t(ms)); Please check full-text and modify them.


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

Input:
Title: A NEW LEPTOCERATOPSID DINOSAUR FROM MAASTRICHTIAN-AGED DEPOSITS OF THE SUSTUT BASIN, NORTHERN BRITISH COLUMBIA, CANADA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors have made all of the necessary comparisons with other taxa, and the figures are generally quite helpful for evaluating their morphological descriptions. Overall, the text is clear and concisely written.

See general comments for additional suggestions and explanations.
Experimental design: The phylogenetic analysis should be expanded and updated. I would strongly advise including the specimen into a more comprehensive ornithischian phylogeny, such as that of Han et al. 2018, to test the placement of this fossil as a ceratopsian. Additionally, I would suggest using the Morschhauser et al. 2019 matrix either in addition to or in place of the current matrix. (I do not fault the authors on this latter point, because it was only *just* published on the week that I completed this review, and none of us had access to it prior to them). Finally, no matter which matrix is used, the robusticity in the placement of RBCM P900 should be explored through various constraint tests (e.g., constraining the fossil in different phylogenetic positions--how many extra steps to place it outside of Leptoceratopsidae?).

See general comments for additional suggestions and explanations.
Validity of the findings: The stated autapomorphy for RBCM P900 and its associated taxon related to phalangeal proportions is not supported as automorphic by the measurements in the supplemental data (e.g., for USNM 13863 and also CMN 8889, which comes close to approximating the same proportions), and should be explored in more detail. Based on the data in this paper, the distribution of the character seems to be broader than implied by the diagnosis (see explanation below), and is variable within a single taxon (e.g., CMN 8887 vs. CMN 8889). This point is critical for whether or not a new taxon should be erected, and must be addressed (in my opinion). At a minimum, I would suggest removing the distinction of "autapomorphy" and instead note that the taxon is distinguished by a unique combination of characters (rather than any particular individual autapomorphy). A more drastic change would be to simply designate the material as Leptoceratopsidae indet.

See general comments for additional suggestions and explanations.
Additional comments: This manuscript proposes a new identification for a fossil (RBCM P900) from the latest Cretaceous of British Columbia, suggesting that it is a leptoceratopsid. This finding is important both because the Cretaceous vertebrate body fossils of British Columbia are so poorly known, but also because leptoceratopsids in general are rather sparse in the fossil record. In my opinion, the assignment to Leptoceratopsidae seems reasonable, although I think that both this point as well as the diagnosis of the new taxon need some additional exploration and clarification. I am not yet confident that this can (or should) be given a new name, primarily because the stated autapomorphy around phalangeal proportions is apparently shared with other leptoceratopsids. Excluding this autapomorphy, there still is a presumably unique combination of characters, but given the fragmentary nature of the material and the uncertainty over intraspecific variation for other leptoceratopsids, I advise caution. This is of course a matter of personal preference, but at the least I think that the manuscript should be updated to address this and other issues outlined below.

General points include:

1) The phylogenetic analysis should be expanded and updated. I would strongly advise including the specimen into a more comprehensive ornithischian phylogeny, such as that of Han et al. 2018, to test the placement of this fossil as a ceratopsian. Additionally, I would suggest using the Morschhauser et al. 2019 matrix either in addition to or in place of the current matrix. (I do not fault the authors on this latter point, because it was only *just* published on the week that I completed this review, and none of us had access to it prior to them). Finally, no matter which matrix is used, the robusticity in the placement of RBCM P900 should be explored through various constraint tests (e.g., constraining the fossil in different phylogenetic positions--how many extra steps to place it outside of Leptoceratopsidae?).

2) The stated autapomorphy for RBCM P900 and its associated taxon related to phalangeal proportions is not supported as automorphic by the measurements in the supplemental data (e.g., for USNM 13863 and also CMN 8889, which comes close to approximating the same proportions), and should be explored in more detail. Based on the data in this paper, the distribution of the character seems to be broader than implied by the diagnosis (see explanation below), and is variable within a single taxon (e.g., CMN 8887 vs. CMN 8889). This point is critical for whether or not a new taxon should be erected, and must be addressed (in my opinion). At a minimum, I would suggest removing the distinction of "autapomorphy" and instead note that the taxon is distinguished by a unique combination of characters (rather than any particular individual autapomorphy). A more drastic change would be to simply designate the material as Leptoceratopsidae indet.

3) The authors have made all of the necessary comparisons with other taxa, and the figures are generally quite helpful for evaluating their morphological descriptions. Overall, the text is clear and concisely written.

SPECIFIC POINTS
- line 77/78 -- full institutional name and location for RAM is Raymond M. Alf Museum of Paleontology, Claremont, California, USA
- for the photogrammetric models, can you provide more details on how they were constructed? How many photos? What settings? What version of Metashape? I don't know that you need a ridiculous amount of detail here, but some basic additional methods should be explained. If relevant, consider including images of the surface models as a figure or supplemental figure; because these models strip away color, it can be helpful for showing morphology (strictly optional, but might be particularly helpful for showing the pedal phalangeal anatomy).
- Consider using the new Morschhauser et al. phylogenetic matrix for ceratopsians, also -- it is more recent, and includes a wide array of characters not included in the He et al. and Farke et al. matrices. Also, although I recognize that at some point you have to cut off the citation chain, the Farke et al. matrix was built on some previous matrices, including those of Ryan and Makovicky (the latter being the primary "grandparent" matrix of all of these), and those should be cited here.
- line 136 -- in general, I do not advocate citation of in review/unpublished papers; maybe just include as "Arbour et al., unpublished data"? Recognizing that you will include more detail in the other paper, I would still include a brief bit of info on how you reassigned the stratigraphic level--was it based on photos? Sketches? Distance from a local landmark? Again, I don't think you need to include comprehensive detail, but because the stratigraphic level is so important here, it is worth providing at least an additional sentence of explanation.
- where element identifications change from those previously published (e.g., the ulna from the previous interpretation of a humerus), please include some justification for why it is a better fit for one element than the other. E.g., morphological features that don't match, etc. This doesn't need a huge amount of text, but should be justified at least briefly.
- As shown in Figure 7H, the penultimate phalanx and preceding phalanx of digits III and IV appear subequal in MOR 542; can this really be used as an autapomorphy for the BC leptoceratopsid then?
- Gilmore 1939 (p. 2) indicates that the pes was articulated when found. This is alluded to in the description (lines 246/247), but should be more explicitly noted. The phalangeal proportions are so critical for this study, that I think it is very important to have some more information on USNM 13863. I have checked my files and don't have any photos, but it is possible that someone else out there might (e.g., Eric Morschhauser or Brenda Chinnery). I do not mandate an in-person visit to the fossil, but I would strongly advise getting more data on this, because it is so critical to the diagnosis and phylogenetic placement. I agree that the AMNH Leptoceratops gracilis holotype is probably not useful given the disarticulated and mixed nature of the material.
- The phylogenetic placement of this specimen should be explored in much more detail. For the ceratopsian analysis, how many steps does it take to move this around Ceratopsia? How robust is its placement as a leptoceratopsid? Are there any synapomorphies supporting this? Also, I would strongly suggest including the specimen into one of the general Ornithischia matrices (e.g., that of Han et al. 2018)--how robust is the placement in Ceratopsia? There won't likely be much in the way of synapomorphies, but I would be interested to see how robust the placement is.
- This is optional, but I would suggest including some basic line drawings showing the pes of the RBCM P900 versus those for Orodromeus, Parksosaurus, Stegoceras, etc., to emphasize the morphological distinctiveness of RBCM P900 from those other taxa.
- Lines 129/130; 229/230; etc. -- Is there *any* chance of additional preparation on those metatarsals? I don't know the matrix or the potential mount of additional material or the logistical feasibility, but given the taxonomic ambiguity of this material, there could (but no guarantee) be important features in this part of the skeleton.
- Although some measurements were included in the previous paper about this specimen, a measurement table would be very helpful here too. I see the supplemental info with this, but at least selected measurements should be in the main body of the manuscript. The supplemental information should be referred to in the text, also. Finally, I would advise reporting measurements only to the nearest 0.1 mm at most precise; the nearest millimeter may even suffice, given limitations in measuring these bones.
- Can you include an interpretive drawing showing the extent of the astragalus relative to the tibia? It's unclear from the photos.
- lines 308-309: Han et al. (2018) provide measurements of the pedal phalanges of Yinlong in the supplemental information, which may be useful here.
- lines 335-342: I don't put a lot of stock into the positions of particular taxa within Leptoceratopsidae; it doesn't take many steps to rearrange the tree (which is frustrating to me, but the reality of current matrices)
- line 411: I liked seeing the acknowledgment of traditional territorial boundaries. I hope this sets a positive precedent within our field!

FULL DISCLOSURE: I had a brief online conversation about aspects of phylogenetic matrices probably relevant to this project with the senior author. It does not, in my opinion, substantively affect my ability to evaluate this manuscript.

CITATIONS
Fenglu Han, Catherine A. Forster, Xing Xu & James M. Clark (2018) Postcranial anatomy of Yinlong downsi (Dinosauria: Ceratopsia) from the Upper Jurassic Shishugou Formation of China and the phylogeny of basal ornithischians, Journal of Systematic Palaeontology, 16:14, 1159-1187, DOI: 10.1080/14772019.2017.1369185

Eric M. Morschhauser, Hailu You, Daqing Li & Peter Dodson (2018) Phylogenetic history of Auroraceratops rugosus (Ceratopsia: Ornithischia) from the Lower Cretaceous of Gansu Province, China, Journal of Vertebrate Paleontology, 38:sup1, 117-147, DOI: 10.1080/02724634.2018.1509866


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 NEW LEPTOCERATOPSID DINOSAUR FROM MAASTRICHTIAN-AGED DEPOSITS OF THE SUSTUT BASIN, NORTHERN BRITISH COLUMBIA, CANADA
Review round: 1
Reviewer: 2

Output:
Basic reporting: Professional language is used throughout, with a few errors (please see annotated copy).
The introduction and background do show context and importance of the specimen, although if there is any way to strengthen the argument for the specimens coming from the site discussed, it would help. This is not an argument for rejecting the paper, as sometimes site information is not available, just a comment. The specimens were found in 1971 and were not discussed until 2008.  Where were they during these years?  The authors state that the original discoverer had field notes that were used to find the probable site of discovery, but only a turtle shell fragment possibly corroborates that this is the area where the specimens were found.  Maybe the authors could share some of the original field notes?
The citations are for the most part fine, although when more than one reference is cited the authors did not put them in alphabetical order at least sometimes (lines 294-296 for example).  Also some areas definitely need more citations, for example the stratigraphic and palaeobiogeographic implications section.  Each taxon listed with an age or formation needs a citation.  I’ve also made notes on the annotated copy.
The figures are great, very clear.  Please double check the scale bars (see below), and I have some specific comments on the figures.
Figure 1 needs clarification on a continental scale, for those of us who don’t live in Canada.
Figure 2 is nice, I like it.  The other figures are also great, although the difference in size of the radii in Figure 4 is surprising (please see the “Validity of the findings” section).
Raw data is supplied and is fine, although I think a different format than an excel file would be more user friendly.
Custom checks: I agree that this is most likely a new species of ceratopsian dinosaur, if for no other reason that it is the only specimen found in this area of the continent.   It is correctly described and meets the ICZN standard.  The autapomorphies in the diagnosis could use some work; one is presence of coossification of elements, which may not be diagnostic (especially when found in another species!), one is reliant on two elements being from the same specimen, which I am not sure of (see “Validity of the findings” section), and one is stated as “similar to” the condition found in two other species.
Experimental design: Research is within the scope of the journal.
No experimentation was done, methods seem sound, although direct measurements of elements were not described in terms of orientation of specimens or other testable criteria.  Cladistic methods are also sound, but I don’t agree with some of the characters used in the analysis.
Many characters in this (and other) cladistic analyses are quite subjective, including words like “short” or “shorter” and “less” or “more”; these analyses are difficult to replicate, because of opinion as to what the words mean.  It would be better to use percentages or other numerical data to differentiate character states, so that everyone who uses the character matrix is in agreement.  However, I realize that I am in the minority on this issue, and the matrix in this manuscript is perfectly acceptable to most.
I caution the inclusion of all characters of the head (which is the vast majority of characters) because this new specimen has no cranial elements included with it.
It would be interesting to run a cladistics analysis with only the characters present on the new specimen, to see what the results of that are.
Validity of the findings: The specimens are definitely valid as possible elements of a new non-ceratopsid neoceratopsian. The fact that they are so fragmentary does not argue against their validity (I might be in the minority with that opinion), because it is unlikely that more specimens will be found from the area. I regret not describing the postcranial skeleton of Prenoceratops before the specimens were scattered across the globe.  It would help this and other papers and projects.  One problem with the Prenoceratops material is that there is quite a bit of individual variation among the elements.  For example, fusion between elements is variable; one scapula and coracoid are fused, while the others are not.  Fusion of elements, as discussed by these authors (and me previously), is not for sure an indication of maturity.  I don’t personally think that it is taxonomically valid, either, and if this is the case then the authors should retract that character from their cladistic analysis.

I have doubts about the bone fragments all belonging to the same fossil.  The RBCM P900 radius is much shorter than that of CMN 8889.  In fact, I’m not sure that the scale is correct for Figure 4.  The length measurement listed in Table 2 for the RBCM radius is 134.9mm, which is 84% of the length of the CMN radius (as listed in the same table).  When I measure directly from the figure, the RBCM radius is 74% of the length of the CMN radius, although this could be due to scaling issues on my part.  Regardless, the radius is much shorter and is also a different color (I know, could mean nothing), but the partial ulna with RBCM certainly appears to be similar in size, if not larger, than that of CMN 8889.  If the authors do include this element with the specimen, then I believe it merits a discussion of what it means that it is so much shorter than that of the CMN specimen.
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: VECTOR DISTRIBUTION AND TRANSMISSION RISK OF THE ZIKA VIRUS IN SOUTH AND CENTRAL AMERICA
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: The authors address an interesting question regarding the potential to predict Zika virus transmission risk in South and Central America. Given its social and health impacts, the ability to understand and manage ZIKAV transmission is an important knowledge gap.  However, the authors do not present the methods in such a way that they can be sufficiently understood and reviewed. There is very little information provided about the model benefits and parameterization. How well did the models perform? The lack of detail additionally prevents robust comparison between different areas at greater or less risk of spread of the ZIKAV infection. A clear, consistent and comparable thresholding process is critical to advancing our understanding of risk. Also, there are lots of issues (grammatical and collocation of words) in some areas of the paper.
Abstract:
Compared to the Background and Methods, Results and Conclusion are too short.
Introduction:
In the last paragraph finish Introduction with possible implications of your study.
Materials and Methods:
You need to clarify why you have selected MaxEnt for the modeling, based on what kind of benefits. Also, clarify the setting you have used to perform the MaxEnt model.
Line 90: I’m not sure whether it matches with the citation guideline, but I guess it is better to move out the authors from the parenthesis: “following the approach suggested in Messina et al. (2015)”.
Line 93: specify how many points were obtained from the references and what kind of pre-processing did you perform to prepare them for the ENM analysis.
Line 103: change ‘worldclim’ to ‘WorldClim’.
Line 103: specify the resolution of the climatic variables used for ENM.
Line 106: Correct quotation at the beginning of „GlobCover 2009 land cover map”.
Line 115: change ‘packages’ to ‘package’.
Line 122: put the name of authors out of the parenthesis.
Line 122: specify how many points were obtained from the references and how many remained after the spatial screening.
Line 124: change ‘was accounted for’ to ‘was used for ENM analysis’.
Line 133-134: repeated usage of ‘account for’! for example in line 134 change ‘we accounted for’ to ‘we used’.
Line 149: remove comma after (https://www.cdc.gov/).
Results
In the Results you haven’t mentioned the predictive performance of your models at all!! At the very least, you need to report the AUC of the performed models.
You have scrimped the geographic pattern of ZIKV transmission risk to some general addressing. You need to report high-risk areas more specifically. For example, you can classify the risk maps to four equal interval classes (e.g. no-risk, low-risk, moderate risk, high-risk), calculate areas of each class and report this area at a country scale. By doing so you can specify countries with highest areas of suitability, i.e. ZIKV transmission risk, more narratively.
Line 204-205: report the AUC of the models for vector species.
Line 212-214: the ECM approach is not a modeling procedure. Replace ‘were modelled’ with ‘were assigned’.
Line 297: This citation is not listed in the References list. Besides, you don’t need to mention the complete name of the reference. You just need to refer to its authors in the main text.
Line 329-330: ‘which is a major point of criticism of correlative approaches in disease modelling overall’ this sentence needs a reference.


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: VECTOR DISTRIBUTION AND TRANSMISSION RISK OF THE ZIKA VIRUS IN SOUTH AND CENTRAL AMERICA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The citations given for a lot of statements tend to be from reviews rather than citing the original primary evidence.

The discussion section has a lot of repetition of the method of results of the paper, while limitation focus on more general limitations of data or classes of models rather than being specific to their analysis.

Introduction: missing a section on previous work and what specific modelling advance is being made in this paper.
Experimental design: No measures of absolute predictive performance of the aedes or Zika models are given. This is key and necessary bit of information for presentation of any predictive model.

Line 187: “the higher the incidence rates of dengue, the higher the incidence rates of Zika (due to co-infections)” – I think co-infections is probably the wrong focus here. I think the more convincing argument about why they would co-occur is that they share the vector and probably similar risk factors. There is also some evidence that dengue can be protective against Zika infection (e.g. Rodriguez-Barraquer et al. Science 2019), so this would argue against imposing a monotonic constraint on this variable.

Line 162: what was the date range for evidence included in the ECM analysis?

Line 125: why the first 9?

Line 114: give some more methodological details about how “rasterPCA” performs PCA

One major criticism of this work is the lack of detail given on the modelling approach. The authors appear to have used the MaxEnt software without any customization to this specific application. The statement that it has previous been used for other species distribution modelling examples is not sufficient given the unique nature of the Zika datasets which were collected in an international public health emergency and I cannot see any adjustment of the datasets used to consider their specific nuances in this analysis. A big concern here would be the highly variable reporting practices for Zika that vary across space and time (particularly early in the outbreak). No attempt has been made to adjust the model to account for this or assess sensitivity to such biases. I couldn’t find any information on how background points were generated- this is key in assessing how observation bias was included.
Validity of the findings: Line 313: “the importance of temperature for the ZIKV transmission risk is very low” – given temperature variables also went into the aegypti and albopictus models it is likely that these covariates soak up the variance that would alternatively have been explained by temperature, therefore I’m not sure this inference is correct.

Figure 4: the Brazilian state of Pernambucco has a low EC value, despite reporting many Zika and microcepahly cases (see Pubmid ID: 27812648).

Line 204: “good accordance with the patterns of their observed occurrence data” – need to give some statistics to justify this, a visual comparison is inadequate – AUC?
Additional comments: Figure 5: why map truncated in N. Mexico?

Figure 3: can’t see the risk maps with the dark points- maybe put on a separate map or use just circle outlines? Plotting background points would also be useful to see what the model is trying to discriminate between.

Line 41: “tourism” -> “travel” – seems unfair to single out tourism

Line 49: “As symptomatic ZIKV infections have only occurred rarely” – strange phrase, do the authors mean only a small proportion of cases are symptomatic – if so state how much and give reference(s). I would also disagree that this is the reason why it has been “of limited public health importance” – this is more due to previous outbreaks being limited in size and poor birth defect surveillance in areas where it is transmitted.

Lien 55: citation after “recongnized.”