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: REGULATING THE UAS/GAL4 SYSTEM IN ADULT DROSOPHILA WITH TET-OFF GAL80 TRANSGENES
Review round: 1
Reviewer: 1

Output:
Basic reporting: This is a good idea that introduces a new method for the temporal regulation of GAL4/UAS based transgene expression in Drosophila. The potential for this method is enormous in my opinion. I believe that this new approach to temporal transgene control will be of great utility to many fly researchers, but still need to present more “specific” GAL4 lines to proof this idea. However, the paper should be significantly edited; really they should re-write it entirely.
Experimental design: As describes, the results of UAS-grim lethality test reveals that it’s unstable lethality ratio displayed not only in each independent experiment but also under copy number of DJ146 or DJ147 (tubulin 1alfa and actin 5C promoter). The applicability of lethality caused from grim gene been concerned. Improving grim function or change lethal gene in here are suggested.

The author notices that insufficient Gal80 maybe cause by tTA uniformly distributed, molecule number of Gal80 (driver copy number), not overall overlap between Gal80 and grim expression region which under driver controlling. But it is interesting about that grim cannot blocked effectively by Gal80 even in the same tissue or same cells although Gal80 expression level is more far than the expression level of grim. Would you refer possible reasons to explain it?

I'm sure that the field would like to know how long it would take to turn expression off again by removing the drug from the food.
Validity of the findings: Does the "tet-GAL80 inducible system” by rtA-tetracycline showed more efficacy precisely expression? I suggest that more specific GAL4-driver confirm is needed. Would be better supported these evidences if the GFP fluorescence results were quantified and if the specific criteria used for the comparisons were defined, when compared with the conventional TARGET system by tub-GAL80ts under permissive temperature? The stereotyped nature of the olfactory lobes and mushroom bodies should make objective quantification of reporter in the relevant glomeruli/neuropils feasible for these assays (Kuo et al., PLoS One. 2012; 7(12):e50855). But even if the contention that TARGET system gave higher expression levels would be a most welcome addition to this study.

The authors should report specific P-values for all statistical tests, either in the results section or the figure legends.
Additional comments: The writing is confusing and the organization of the data is not very good either. I suggest that they fully re-write the paper starting with a results section that describes the reagents carefully, which does not need to be long but clear. The set of data is coherent, but too dense. The message they want to convey will be clearer after a serious trim showing a synthesis of the principal results. This ms should be rewrite or significantly edited.


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: REGULATING THE UAS/GAL4 SYSTEM IN ADULT DROSOPHILA WITH TET-OFF GAL80 TRANSGENES
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: In this manuscript, the authors describe a new approach to regulate gene expression in Drosophila using a tet-off Gal80 system. It complements the currently available tools such as Gene-switch or temperature sensitive Gal80 to control the temporal activity of Gal4. They provide detailed analyses on the new system in the result and supplementary sections. The tet-off Gal80 system requires multiple transgene (>2 copies) to obtain high level of Gal4 inhibition, which makes the system not very practical in its current state. However, it provides a proof of concept and a foundation for the research community to improve and optimize the system. There are some general concerns and suggestions to the authors that they may find useful.

General concerns:
1) Does the chronic tetracycline treatment have any detrimental effect? Do the authors have any information about the dosage effect on lifespan or behavior (e.g. minimum effective dosage)?

2) Do the author have any information about the efficiency of the CMV1-TetO promoter in pDJ146/147? The reported low efficiency in suppressing Gal4 using these two constructs comes a little bit surprising.

3) The authors may want to consider rearranging some of the supplementary and result figures. In fact, some of the supplementary results are more informative (e.g. SFig 13, 14 – demonstrate the effect of inducer; STable 15 – effect on various Gal4 lines) than result figures (e.g. Fig 2 - not very informative unless you also show the expression pattern with pDJ146/147, with/without inducer).

Specific comments:
1) The layout of Figure 1A is a little confusing. The authors could simplify the figure by showing  progenies on one side (tet on) and the other side (tet off). “Hexagon” in the figure text should be “pentagon”.

2) It is very helpful for the authors to provide figures to every step in the construction of the transgenes. The authors could consider simplifying them by removing some of the irrelevant restriction sites but provide the final, full sequence information of the constructs pDJ146/147. The author may also want to consider using Gibson assembly to generate complex transgene constructs next time.

3) It is quite surprise to see pDJ147, with actin5c promoter, has no expression in the CNS (fig 6)? Could it be a positional effect specific to this transgenic line?

4) In figure 8, does the flies have UAS-grim? If not, it should be removed from the figure text?

5) In supplementary tables (e.g. STable 9,10), it would be better to show the actual measurement and highlight the one in bold to show the significance. Showing the P-value only without the actual number is not very informative.

6) The background of Figure 6 is too dark in some panels. It would be helpful if the authors can fix 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: REGULATING THE UAS/GAL4 SYSTEM IN ADULT DROSOPHILA WITH TET-OFF GAL80 TRANSGENES
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: This is a brilliant study that introduces a new method for the temporal regulation of GAL4/UAS based transgene expression in Drosophila. The potential for this method is enormous in my opinion. Authors replied all the points that I asked and showed reasonable results. I think this manuscript is ready to be published in PeerJ. I believe that this new approach to temporal transgene control will be of great utility to many fly researchers. It is a significant and welcome contribution to the field.


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: CD4 COUNT AND TUBERCULOSIS RISK IN HIV-POSITIVE ADULTS NOT ON ART: A SYSTEMATIC REVIEW AND META-ANALYSIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper is well written, but can be improved with minor copy-editing.
Experimental design: The study objective and rationale for this study and study design methods are well stated.
Validity of the findings: The analysis is sound, but the findings have to specifically stated that they are applicable only to HIV positive adults (>= 15 years of age) not on ART, rather than generally to all people living with HIV not on ART, since this can be misunderstood to mean both children and adults.
Additional comments: The authors have conducted a systematic review and meta-analysis to quantify the risk between CD4+ T cell count and tuberculosis among HIV-positive adults (>= 15 years of age) who are not on antiretroviral therapy. This is a valuable study that quantifies this risk in a systematic manner, and adds the the current evidence illustrating the exponential increase in TB incidence with declining CD4+ T cell count.

Here are my specific comments:

1. Lines 1-2 -- Title: Change the “people” in title to “adults”, since this study is specific to HIV-positive adults (>= 15 years of age). You can change the title to “CD4 count and tuberculosis risk in HIV-positive adults not on ART: A systematic review and meta-analysis”

2. Line 4 -- Short title: Change short title to “CD4 count and TB risk in HIV-positive adults not on ART”

3. Lines 30-32: Add “among HIV-positive adults (>= 15 years of age) not on ART” to the end of the sentence, (i.e), change sentence to “Our meta-analysis estimated a 1.43 (95% credible interval: 1.16 – 1.88)-fold increase in TB incidence per 100 cells per mm3 decrease in CD4 cell count among HIV-positive adults (>= 15 years of age) not on ART”

4. Line 33-35: Add “among HIV-positive adults (>= 15 years of age) not on ART”, (i.e), change sentence to “Our analysis confirms previous estimates of exponential increase in TB incidence with declining CD4 cell count among HIV-positive adults (>= 15 years of age) not on ART, emphasizing the importance of early ART initiation to reduce TB risk.

5. Similar to comments 1-4, please change any reference throughout the paper from people to make it specific to adults. Thereby, the analysis and findings in this paper will not be misunderstood to be applicable to all people, including children and adults.

6. Line 43-45: Be clear there are a total of 1.8 million deaths from TB, of which 1.4 million deaths are among HIV- people and 0.4 million deaths among HIV+ people.

7. Line 154-156 and Figure 4: Why is the upper CD4 T cell count of 1000 cells/mm3 used? Can’t the curve be projected/extrapolated using the available data?

8. Line 293-294: Add “except for one study (Wolday et al. 2003)”, (i.e), modify the sentence to “BCG vaccination status was not reported except for one study (Wolday et al. 2003), and may itself have confounded results, either through variation in coverage or variation in efficacy.”

9. Figure 1: Update the box “Studies included in qualitative synthesis (n=7)” to “Studies included in qualitative and quantitative synthesis (n=7)”.

10. Figure 2 legend: Change “people” to “adults (>= 15 years of age)”.

11. Figure 3: Try the plot with X axis in linear scale instead of log scale for “Increase in TB incidence per 100 CD4 cells/mm3 decrease” -- This is likely to represent this data better for understanding. If the current plot (log scale) is a better visualization of this result, than leave it as is; if not replace it with the linear scale plot.

12. Table 1: Split the “Study description” column to “Study description” and “Conclusion”. That is, add a separate column for “Conclusion”, and move this corresponding text from the “Study description” column.

13. Table 1: Monge, 2014 study -- age range is > 13 years. Is the overall systematic review representative of >=15 years of age or >=14 years of age?

14. Table 1: Nicholas, 2011 study -- Name all the 6 countries in the “Country” column.


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: CD4 COUNT AND TUBERCULOSIS RISK IN HIV-POSITIVE ADULTS NOT ON ART: A SYSTEMATIC REVIEW AND META-ANALYSIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: in line 109 they say they excluded studies where the majority of HIV infections are known to be not HIV-1; I think it should be clarified to the reader what HIV-1 means.
 In line 194 it says "The studies used previous analyses" while I think it should say "The studies used in previous analyses"
Experimental design: I think the purpose of the study is clearly stated. Methods are explained in such a way that allows other researchers to reproduce or further explore the topic.
Validity of the findings: Theay clearly state how their findigs relate to previos results in literature, explaining where their findigs confirm what was reported before, and highlighting  new possible paths  for further understanding the topic.
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: UNRAVELING THE STRUCTURE AND COMPOSITION OF VARADERO REEF, AN IMPROBABLE AND IMPERILED CORAL REEF IN THE COLOMBIAN CARIBBEAN
Review round: 1
Reviewer: 1

Output:
Basic reporting: The ms "Unraveling a resilient reef: structure and
composition of Varadero, an imperiled coral reef in
the Colombian Caribbean" describes a community of organisms on a newly disovered healthy reef in close vicinity to the outlet of the Magdalena river, Colombia.

It is unclear why the term "resilience" is used, which implies that recovery has taken place. Since the reef has just been discovered, it is unlikely that this can be established. Perhaps the authors like to suggest that the reef's good condition indicates that it has been offering "resistance" to local threats?

The report is descriptive and mainly of local importance. The discussion could be made more interesting for a wide readership by including comparisons with other areas in the region or elsewhere of reefs in the vicinity of river discharge or in murky water (e.g. Amazon river, Singapore, Jakarta Bay, etc.). Are such reefs in other areas healthy or degraded? Have healthy reefs shown resilience?
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: Additional remarks are mentioned on the ms pdf.


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

Input:
Title: UNRAVELING THE STRUCTURE AND COMPOSITION OF VARADERO REEF, AN IMPROBABLE AND IMPERILED CORAL REEF IN THE COLOMBIAN CARIBBEAN
Review round: 1
Reviewer: 2

Output:
Basic reporting: I found the manuscript to be well organized and clearly written, only finding minor grammar errors. The paper reports on the benthic (sponges, coral, and algae) and fish assemblages of a newly discovered, and apparently highly resilient coral reef inhabiting the highly polluted waters within Cartagena Bay.
Please consider the following edits:
1)	Within lines 30-33, including both the total number of sponge and coral species found at Veradero Reef.
2)	Within lines 51-57, authors give examples of reefs found in extreme environmental conditions, yet there is not a single example of a reef being exposed to anthropogenic stresses similar to Veradero Reef. I recommend the authors to consider Appeldoorn et al., 2015 “Mesophotic coral ecosystems under anthropogenic stress: a case study at Ponce, Puerto Rico”.
Experimental design: The experimental design as also well organized and clearly written. The survey design and statistical analyses for benthic and fish assemblages were correctly implemented.
There are several additions and modifications that I would ask the authors to consider:
1)	Line 89-91 Possibly rephrasing the sentence to/similar: Data from the GPS instrument was downloaded and analyzed using the GIS software Garmin BaseCamp, from which a detailed map of the reef was subsequently produced (Figure 1).
2)	Line 94 Possibly rephrasing the sentence to/similar: Annotations of coral community composition at multiple depths was analyzed as in Geister (1977).
3)	Line 95 – to emphasize and not confuse the reader, please include the name of the reef. “.. a detailed profile of Veradero Reef’s coral …”
4)	Line 125 – replace the word “later” with the word “downstream”
Validity of the findings: The results of the study are reasonable given the experiments performed. I congratulate the authors for including marine sponges within the surveys and analysis, they are usually left out of major and important survey efforts, even though they are an important component of any coral reef ecosystem.
Additional comments: First and foremost, I found this paper extremely interesting, especially since it highlights the discovery of a reef which seems thrive in volatile and toxic environment. As the authors state, Veradero Reef should be protected, I believe that the Colombian government and its citizens should take pride in this newly discovered coral reef, and enforce protection laws against the destruction of this resilient coral reef by the proposed dredging of the Cartagena Bay.

I do however, have several comments for the authors to take into account:
1)	Line 190 – the genus Helioseris (correct) is misspelled.
2)	Line 193 – the genus Undaria is no longer valid and should be replaced by Agaricia
3)	Same for lines 194, 202, 207, 210, 211, 227, 232, 233,
4)	Same for Figure 2 – Undaria should be changed to Agaricia
5)	Figure 2 – genus Helioseris should be corrected
6)	Line 225 – replace word “are” with “were”   “..were also observed.”
7)	Line 226 – start sentence with “In total, 38 coral species…”
8)	Line 226 – after the word “identified” add the words “at this depth”
9)	Line 235 – I am a confused by this sentence. The authors state that in total, there are 50 sponge species were observed at Varadero Reef, yet, there’s 38 species listed in parentheses. Maybe the authors meant to say that in total, “69” sponge species were observed?
10)	Line 237-238 Proposed sentence: Survey transects at upper shallow terraces in Varadero Reef showed higher sponge species richness than that of upper shallow terraces in Baru Reef; 36 and 25 species, respectively.
11)	Line 289 – see de Bakker et al. 2016 “40 Years of benthic community change on the Caribbean reefs of Curacao and Bonaire: the rise of slimy cyanobacterial mats” to possibly cite a decline in coral cover.
12)	line 291 – a comma is needed within the reference after et al.
13)	line 346 – I recommend switching the words “be not” to “not be”
14)	Figure 4 – on the X-axis, change the word “Life” with “Live”
15)	Within S1 – replace Undaria with Agaricia
16)	Within S1 – Porites astreoides is misspelled
17)	Within S2 – Amphimedon is misspelled


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: UNRAVELING THE STRUCTURE AND COMPOSITION OF VARADERO REEF, AN IMPROBABLE AND IMPERILED CORAL REEF IN THE COLOMBIAN CARIBBEAN
Review round: 2
Reviewer: 1

Output:
Basic reporting: See previous review
Experimental design: See previous review
Validity of the findings: See previous review
Additional comments: The paper has been improved. It reads very well. The illustrations are very nice. I like the artwork in figure 2.  Because the ms is almost ready for publication, I congratulate the authors.

However, I have found some minor issues for possible improvement. They are indicated in the word document.

Based on two remarks in the margin, I have explained the importance of a hyphen. This is not always a matter of personal style.

The authors did not take care of the reference list as suggested in my first review. In several references, the spelling of the names of authors is incorrect. In many references, the names of authors still lack initials. I have marked some examples.

I have also checked the supplementary material. I suggest that  taxon names in tables should be presented in alphabetical order.


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: MOTOR PERFORMANCE IN PRADER-WILLI SYNDROME PATIENTS AND ITS POTENTIAL INFLUENCE ON CAREGIVER’S QUALITY OF LIFE
Review round: 1
Reviewer: 1

Output:
Basic reporting: The majority of the manuscript is clear and unambiguous. I have a few suggestions on grammar and language.
1. Please use "patient first" language throughout the manuscript. For example, line 54 should read "the child with Prader-Willi" instead if "the Prader-Willi child".
2. The correct term is "hand grip strength", not "hand gripping strength" (example, line 35).
3. Line 54: The statement that excessive eating begins in infancy is incorrect. Increased interest in food has a median age of onset of 4.5 years and hyperphagia 8 years (Miller et al., American Journal of Medical Genetics, 2011). In infancy most patients with PWS have poor feeding, with or without failure to thrive.
4. line 64 - change to "with an increase in body fat mass"
5. line 73 - change to "devote time and effort to care for them"
Experimental design: 1.The researchers do not present an a priori hypothesis. They aimed to investigate the relationship between motor performance and primary caregiver QOL. There were 80 correlations examined in the analysis section. Was there a particular relationship that was of interest? Or was this an hypothesis generating exercise?
2. The question is interesting and attempts to address a knowledge gap.
4. The patient population was adequately characterized.
5. Validated measures were used.
Validity of the findings: 1. The researchers analyzed 80 correlation coefficients and did not correct for multiple hypothesis testing or specify and a priori hypothesis/primary outcome. It is not surprising that 5 of 80 results had a p-value <0.05 as this approximates the expected false positive error rate. The conclusions presented in the discussion vastly overstate the meaning of these results. For example, you could perhaps conclude that these results justify a subsequent study to test the relationship between upper limb muscle strength in patients with PWS and their caregiver's bodily pain. It is not appropriate to conclude that better upper limb muscle strength in PWS lowers the intensity of caregiver's pain (lines 215-218).
2. Lines 240-246 -The authors state that a TUG test time <20 seconds indicates that an individual is independent for basic transfers. All PWS patients in this study had a TUG time <20 seconds so how can we draw any conclusions between the TUG test results and caregiver social relationships?
3. I suggest using a composite score from each of the 3 quality of life measures, rather than 16 subscales. If that's not possible, the conclusion should acknowledge the multiple hypothesis testing and need for further research rather than making strong conclusions based on these data.
Additional comments: No additional comments


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

Input:
Title: MOTOR PERFORMANCE IN PRADER-WILLI SYNDROME PATIENTS AND ITS POTENTIAL INFLUENCE ON CAREGIVER’S QUALITY OF LIFE
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors address an important topic to Prader-Willi, namely, the impact of adult patients’ physical disabilities on their family/caregiver quality of life

	There are a number of errors in grammar and syntax noted. As such, the manuscript would benefit from extensive professional and/or peer editing.

	The introduction introduces the phenotype and disabilities of PWS, however misstates several particulars. On line 54, the authors state that during infancy the Prader-Willi child starts excessive eating. In reality the hyperphagia of PWS usually starts in school age children, not infancy (Genetics in Medicine, 2012, 14(1):10-26). In addition, PWS is not cause by the deletion of a “specific gene” as the authors state on line 59, but a specific gene region which includes a number of potential genes leading to the phenotype.

	I would like to see the authors expand upon the knowledge gap being filled and be more explicit in stating their hypothesis and why this is important to know.
Experimental design: 	Authors state on line 166 that seven individuals were recruited but on line 167 only describe 2 females and 4 males. Table 1 shows 5 males and 2 females.

	The authors state that all patients and their caregivers were recruited through the PWS Association. I am concerned that this may introduce significant recruitment bias as those who participate in such associations may be more engaged and adjusted to the difficulties of caring for family members with PWS. This bias combined with the small numbers in this study severely limit the applicability of these findings to the general PWS population. I would very much like to see additional study participants recruited through other means such as genetics or endocrinology clinic. Minimally, the authors should address this shortcoming in the Discussion.

	The authors do a good job of outlining the various physical and QoL tests performed as part of the study.

	I would like the authors to comment on the use of handgrip and lateral pinch strength tests in the PWS populations. Have these been validated as tests of upper limb muscle strength in PWS? Given the atypical hand morphology of PWS (brachydactyly with interdigital webbing and joint laxity) could these tests be interrogating hand dexterity more than upper limb strength in these patients?
Validity of the findings: 	In lines 210-218, the authors discuss the correlation between grip strength and caregivers’ pain as assessed by the SF-26 results. I would like the authors to expand on their discussion regarding these results. Why was there no correlation with the Pinch test? What domain of upper limb strength or manual dexterity is the Grip test assaying that the Pinch test is not? Are these results expected or not? Why or why not?

	The authors correctly identify the limitations of this study in lines 255-260. These limitations severely curtail the general applicability of these results. Not only are the study numbers extremely small but there is no control group of any type. Are there similar studies that have been carried out in similar populations that the authors can contrast their results with? Other obese populations? Other disabled populations?

	If these results were to be validated, what specific changes in patient care might be made to help mitigate these detrimental effects on caregiver’s QoL?
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: COMBINING OCCURRENCE AND ABUNDANCE DISTRIBUTION MODELS FOR THE CONSERVATION OF THE GREAT BUSTARD
Review round: 1
Reviewer: 1

Output:
Basic reporting: The study forecasted the spatial occurrence as well as the abundance distribution of Great Bustard based on the priority protection index (PI) by combining occurrence and abundance indices. The results show that the occurrence and abundance models display different spatial distribution patterns, and PI could guide the protection of the areas with high occurrence and high abundance. Generally, the MS did not tell me how to combine the occurrence and abundance indices, and display clearly spatial distribution pattern. Furthermore, only based on the distribution data of Great Bustard in Bohai Bay, the author confirmed that the findings have a wide relevance and applicability, worldwide, and it was difficult to be a global research template. This is strongly non-robust.
In Introduction part, the author need to clearly show why many scholars found species occurrence and abundance distribution not to display similar patterns, conservation decisions based on SDMs predictions are insufficient and may even be misleading? And why one time-critical challenge and associated progress will be centered how to combine the useful information that SDMs and SAMs? And one of the objects of the MS was to assess and develop models to predict accurately the patterns of bustard occurrence and abundance. But in Method part, you just used the Random Forest model, no any information about the developing model, if you developed the model, please give detailed information of developing, if not, please describe your method accurately.
Experimental design: I don’t know how you choose the eleven environmental variable? Why these variables, not other variable? And why eleven, not ten or eight, or other? This need more details.
About the experimental design, you said “we travelled with a small four-wheel-drive tractor along fixed routes”, can you give the detailed information about the route line design context. Actually, this is key for your data robustness.
Validity of the findings: Results are not well stated linked to original research question. In Introduction part, you mentioned the second object of the study was to predict accurately the patterns of bustard occurrence and abundance, but in Result part, you did not give clearly the pattern? Why? I suggest you describe your predicted pattern in the Result part.
Additional comments: Line 25, best-available presence and count records for an endangered farmland species, Great Bustard (Otis tarda dybowskii) in Bohai Bay, China, as a case study. How did you proved that presence and count records for an endangered farmland species was best-available? And line28, how you know the method was a powerful machine learning method? Can you give some illustration?
Line 30-31, You mentioned that the environmental variables influenced bustard occurrence and abundance differently. How the variables influenced? And you found that occurrence and abundance models display different spatial distribution patterns. Please give actually pattern, what pattern would be displayed?
Line 36, only by your case study, how to confirmed that your findings have a wide relevance and applicability, worldwide. That means how to extend you scale from the local Bohai bay to worldwide scale?
Line 91, The topographical and climate condition varies little in the study area. Can you give information about how varies little?
Line 99, According to my knowledge, the bustard distributed widely, why you said Bohai bay is the world’s largest wintering ground ? Is it based on your research or other people’ research? And why is representative of the typical farmland situation in the North China Plain. Can you give actuately base or literature?
Line 123-124, please give more detailed information about how to construct a distance layer for these variables using the Euclidean.
Line 135-136, Please give detailed information that what range of NDVI representing good condition vegetation, and what range of NDVI represent the bed condition of vegetation, and why?
In line 139-155, there are many expression need to be confirmed, such as advanced (line 139), robust (line 141), very good (line 142), performed the best (line 144), robustness (line 146), not so good (line 148), better (line 151), best (line 153). All of these evaluation were based on your own judgment but not citation or proof. I suggested you should rewrite this part.
Line 47, you constructed initial abundance model, but you did not tell us how to construct the model?
Line 158, you adjusted the simulation abundance, can you give more information about how to adjusted the simulation?
Line 171, you extracted the habitat information, in line 172 you created a model file, and in line you adjusted the predicted abundance, can you tell us how to extract, create, and adjust?
Line 182, what is better?
Line 195, what is the more suitable and scientific? What is not suitable or scientific?
Line 258, how do you know the habitat had a fragmented distribution?
In Discussion part, some sentence is no cited literature, such as line 264, 366-367, and more. Please check.


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: COMBINING OCCURRENCE AND ABUNDANCE DISTRIBUTION MODELS FOR THE CONSERVATION OF THE GREAT BUSTARD
Review round: 1
Reviewer: 2

Output:
Basic reporting: This research looks at an endangered species and proposes a way for better conservation management. In the manuscript, the authors have done a good job to illustrate their design, data collection, methods for modelling, discuss the results and future implications. The references are thorough and figures are informative.
Experimental design: The design of the study is generally clear. However, the authors need to address the following questions. First, what is the reason and reference to use a linear regression to convert observation abundance to another? You just want better prediction or other reasons? Why not transform the abundance data before according to its distribution (zero-inflated)? Second, why choose random sampling for pseudo-absence? Do you control for the distance between presence and the random absences? Third, how do you validate your model? Do you have other independent dataset to validate it? Fourth, for this mobile species, for the same survey, how do you avoid counting the same individuals in different sites?
Validity of the findings: The findings are useful in conservation planning, especially the way to combine two different kinds of information: presence and abundance. The author could illustrate this findings more, what is the consequences of just using species distribution model or abundance model compared to using the combined result? You can threshold the two maps and compare the differences.
Additional comments: It is a good study. I have put other comments for the wording of this paper. Please address this issues and work on the language more carefully.

Line 35: spell out the rel.
Line 73: Delete “Farmland”. This species habitat contains both grassland and farmland.
Line 101: delete “situation”
Line 105: delete “winter survey”
Line 115: How do you avoid record same individuals during the survey?
Line 125: change spacing to pixel size.
Line 156: Is there any reference for this method (using linear regression converting observation to simulation abundance)?
Line 166: There are various ways to choose pseudo-absence. Why use random sampling? Do you control the distance between absence and presence?
Line 210: rephrase the sentence. Not clear what you want to say.
Line 215: rephrase this sentence.
Line 220: What is multivariate package? Not sure what it refers to
Line 263: change “!” to “.” Not common to use “!” in academic paper.
Line 276: Please rephrase this sentence. Can’t understand what you mean.
Line 309: You jumped around in this section. The author talked about the birds then jumped to plant and crop later. Please make clear transition.

Figure2. Change the x axis title for b. Is it observation ID?


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: COMBINING OCCURRENCE AND ABUNDANCE DISTRIBUTION MODELS FOR THE CONSERVATION OF THE GREAT BUSTARD
Review round: 2
Reviewer: 1

Output:
Basic reporting: The revised MS  solved the issues I have proposed.
Experimental design: The authors have given detailed informations about the chose of the eleven environmental variable.
Validity of the findings: The conclusions have been stated appropriately.
Additional comments: The authors have replied my questiones detailed.


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: IN SILICO IDENTIFICATION OF OFF-TARGET PESTICIDAL DSRNA BINDING IN HONEY BEES (APIS MELLIFERA)
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article could be significantly improved by reviewing the use of jargon and revising unclear sentences.
A few additional references are recommended.
Experimental design: The authors state in the materials section that search terms included “siRNA,” “dsRNA,” “RNAi,” and “RNA interference.” In the Conclusion, they say outcome can matter depending on "whether the organism is exposed to siRNA or dsRNA". This implies that there is a meaningful distinction that is not made clear in either use of terms or methodology.
Validity of the findings: With clarification of the issue above, I have no further comment.
Additional comments: The paper uses a lot of jargon and that also makes some sentences difficult to understand even for a reader familiar with the jargon.

Please reconsider using the word homology or its derivatives (eg, homologies) when referring to quantitative relationships between DNA sequences. Homology is a conclusion of relatedness by descent and not a synonym of similarity nor a quantitative term (Fitch WM. Homology a personal view on some of the problems. Trends Genet. 2000;16:227-31). There is no ‘degree of sequence homologies’ just as there is no ‘degree of pregnancy’ and no information is lost saying ‘degree of sequence similarity’ instead. Sequences may be similar because they are homologous, or similar because they are similar no matter their histories (e.g “random sequence similarities” (line 156-7)). It doesn’t matter why they are similar for this manuscript only that they are. I know that others do it, but such uses are eroding the precision of the term.

In fact, given that taxonomy is not a predictor of off-target effects, the use of the word ‘homology’ is particularly troublesome.

33-35 This sentence could be expressed as: “The target gene sequences for these pesticidal RNAs were determined, and the degree of similarity with sequences in the honey bee genome were evaluated statistically.”

37-8 “The likelihood of off-target sequence homology increased with the parent dsRNA length.” Please reconsider this jargon. I suggest “The likelihood that off-target sequences were similar increased with the number of nucleotides in the dsRNA molecule.” What after all is the parent dsRNA (also line 137)? Is it the active pesticidal RNA?

38-9 The dsRNA doesn’t bind to the gene (as in DNA). Instead: “Non-target binding of the dsRNA was unaffected by taxonomic relatedness of the target insect to honey bees…”

42-43 Sequence similarity is not enough to predict biological effect, but likewise there are no bioinformatics ways to ensure that a dsRNA will have no effect, too. E.g. because of secondary dsRNA generation in exposed insects, the primary dsRNA may not be the active molecule in the honey bee. This sentence seems to imply otherwise.

57-59 This sentence describes two methods of delivery but likely readers will be unfamiliar with both, especially since to my knowledge there are no commercially available sprays. Consider introducing appropriate references for both.

59-63 This is true if the dsRNA is longer than the active molecule. It does not have to be. It is possible that plant processed or encapsulated dsRNAs may already be 19-25 nucleotides and not require further processing in the insect.

73-74 This is a grammatically challenged sentence. Gene sequences aren’t silenced, genes are. Please revise to something like: “within a non-target species, this unintentional gene silencing can be due to silencing the intended gene in the unintended organism (non-target binding) or silencing a different gene with sufficient sequence similarity to the dsRNA (off-target binding)”

81 What does “even when sequence homology is identical” mean? Does it simply mean ‘even when sequences are identical’?

79-82 This sentence contradicts many reports in the literature that are more recent than 2004. E.g. Hanning JE, Saini HK, Murray MJ, van Dongen S, Davis MPA, Barker EM, et al. Lack of correlation between predicted and actual off-target effects of short-interfering RNAs targeting the human papillomavirus type 16 E7 oncogene. Br J Cancer. 2013;108:450-60.
Unless the authors have other references, this sentence should be removed. The reason bioinformatics analyses have been advocated is not because (82-83) they can avoid false negatives but because they are a starting point to test putative positives. Heinemann JA, Agapito-Tenfen SZ, Carman JA. A comparative evaluation of the regulation of GM crops or products containing dsRNA and suggested improvements to risk assessments. Environment International. 2013;55:43-55.

160-1 Well said. Another good reason to use homology correctly. Moreover, with sprays, non target organisms don’t have to be animals.

162-170 This paragraph is incomplete without discussing secondary dsRNA products. Pak J, Fire A. Distinct populations of primary and secondary effectors during RNAi in C. elegans. Science. 2007;315(5809):241-4. Sijen T, Steiner FA, Thijssen KL, Plasterk RHA. Secondary siRNAs result from unprimed RNA synthesis and form a distinct class. Science. 2007;315(5809):244-7.

Please avoid associating predicted binding with actual binding, as in (line 174-5) “67% of all tested dsRNAs had off-target binding with developmental genes in honey bees” This is more accurately “had the potential bind to honey bee developmental genes that were not the target”. In fact, binding is not the key criterion because one base pair is enough to satisfy binding. Some sense of the strength of the binding should also be imparted to the sentence.

178-9 It is not correct to say that a gene ‘performs’ cell proliferation or apoptosis.

180-2 Yes, but in saying that “in silico analysis identified potential gene targets that could present a hazard” it is important to also say that it is not possible to confirm that all or even most potential unintended targets were identified. This is the first line of the conclusion section, but that is too subtle.

189-192 RNAi is not just ‘gene knockdown’. There are 3 manifestations from RNA degradation (involving siRNAs that have 20-21 nt matches usually in the coding region) to translation inhibition (normally when miRNAs are used, ie, those with 2-8nt in the seed region) and RNA directed methylation. The discussion perhaps would benefit from spelling this out.

191-197 Hanning et al (above) would be a good reference for this paragraph.

200-2. Not if it is a spray.

202-3 What is the difference between what you mean by siRNA and what you mean by dsRNA? The latter is usually the generic for si/mi/shRNA etc. Do you mean processed dsRNAs when you say siRNA? Are you talking about the guide strand?

203-7 And secondary dsRNAs.


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: IN SILICO IDENTIFICATION OF OFF-TARGET PESTICIDAL DSRNA BINDING IN HONEY BEES (APIS MELLIFERA)
Review round: 1
Reviewer: 2

Output:
Basic reporting: GENERAL
The paper fulfills all criteria for professional scientific publication: clear and well written, literature references and structure of paper is professional.

This paper offers important information for risk assessment of an emerging new biotechnology with broad application but also risk potential for insects. The authors carried out database research for published sequence information to determine the degree of homology between target gene sequences of pesticidal active RNAs in a nontarget organism, the honey bee. Honey bees served as an iconic case example of nontarget species with critical socio-economic and ecological functions. Off-target effects of any pesticidal substance must be avoided. The authors tested and validated a new methodology for improving the current risk assessment for nontarget effects that are not geared to assess these new biotechnologies. Therefore, I consider this work very important and recommend publication.

The research method is well described and carried out, the results are very interesting clearly suggesting the potential for nontarget effects in honey bees to occur if they come into contact with the RNAi. Whether or not that will happen depends on the form of delivery of the RNAi - in-planta or as sprayable formulation - and on timing of the application. But the first step is to determine whether there are any sequence homologies and the authors clearly determined that this is the case. Hence, now exposure assessments must follow and should be carried out prior for assessing the full risk potential. All of this definitely merits publication.

My further comments address issues that are not critical to the decision of publication but are for the authors to decide to include if they agree with me that it will improve the paper. Since page numbers are missing I can only indicate line numbers.

INTRODUCTION
Line 67. The authors mention here 'current risk assessment framework' - personally I would appreciate if the authors would not only focus on the US but also include references to the Cartena Protocol Risk Assessment requirements or EU regulatory risk assessment (mandatory for over 160 nations in the world). The US is a singular case having the most lax standards re risk assessment of biotechnology. This might be used as an excuse to reject the applicability of this work/paper to other regulatory systems of biotechnology as being more stringent. However, none of the other regulatory risk assessment schemes in the world would fully caputure these new risks and, therefore, this work is definitely also of relevance beyond the US.

Line 76, last word 'unique' - I suggest the term 'different' instead - and again, also here, reference to other regulatory systems are highly recommendable, so this work has relevance beyond the US.

MATERIALS AND METHODS - see below in next section

RESULTS AND DISCUSSION
Line 153 onward - relating to 'taxonomic relatedness' as an indicator or a criteria for selecting potential nontarget species at risk. This issue drops a bit out of the air, although there is a well-known precedent. This argument for selecting potentially affected nontarget organisms for testing based on their relatedness to the target pest species as indication for susceptibility has long history in the risk assessment discourse of GM Bt plants. And there it has already or also been shown to be a weak indicator for selecting potentially affected nontarget organisms.

In general, I find the authors could connect their discussion and paper in general to the on-going discourse about the already existing GM crop plants. Some issues are indeed the same or connect in other ways. And there are several references that could be cited here in support.

One issue that is still puzzling to me is on the other hand the fundamental difference in these pest control strategies that have not been properly pointed out - at least to my knowledge which is admittedly limited. It is in my view a fundamental difference if a sprayable pesticidal substance is a low molecular weight chemical or protein (in case of Bt toxins) affecting biochemical metabolic processes or life support systems such as nervous signal transmission or breathing apparatus of insects versus this form of pest control where it targets the genetic machinery. I think we have to think about specificity in completely different way whether it targets biochemical pathways or gene functioning. In particular, in my view, this is argument to broadly reject the above mentioned issue of 'taxonomic relatedness' to be in any way indicative of susceptibility. All organisms share a very similar genetic machinery - hence, all organisms are potential nontargets in a much more broader way than it could be argued with a chemical disrupting certain biochemical processes that are unique to say a kingdom of organism or other fundamental categories of organisms (e.g. photosynthesis in plants, breathing in insects vs mammals, aquatic vs terrestrial organsims etc.). I find that this paper may be a good one to at least raise these issues or point to references where these have been discussed - if at all.

The authors are approaching these fundamental questions a little bit in an ad-hoc fashion in the last paragraph of their discussion (before conclusions) within the discussion about what are highly conserved genetic regions in metazoans or not. I think, here a more fundamental discussion along the lines I outlined above would be quite suitable and add relevance of this paper for the general discussion about risk assessment of types of biotechnology applications.
Experimental design: MATERIALS AND METHODS
All is well described but I think the process could be explained better.

Lines 92-94 - the authors list here the search terms for their database search. Did they not include the term 'honey bee' or 'Apis mellifera' or terms refering to target- or nontarget organisms? Later on they list the various species they found published studies for. This means they only looked for anything published on RNAs for pest control and then assessed as part of their analyses which the target species were? And then they set out to compare these (i.e. all RNA applications they found) against the published genome sequences of the honey bees? This process should be explained a bit better, in particular, for readers who are not familiar with this pest control technology.
Validity of the findings: Data is robust and well presented and highly relevant to the field of risk assessment of biotechnological applications and products.

Conclusions are supported by the data shown and linked to the objectives and research questions. In fact, I suggest that the authors broaden their discussion and connect it to an international discussion of regulatory risk assessment requirements to make it clearly relevant beyond the US.
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: EVALUATING THE ROLE OF WILD SONGBIRDS OR RODENTS IN SPREADING AVIAN INFLUENZA VIRUS ACROSS AN AGRICULTURAL LANDSCAPE
Review round: 1
Reviewer: 1

Output:
Basic reporting: The English is clear and professional, the background information and literature are thorough and appropriate, the structure and figures are appropriate. I could not view the raw data file -- it was all symbols for me. I tried on two computers and try to open it as a text file or import it into Excel.
Experimental design: Experimental design: Original primary research is reported, the research question and motivation are clear, the investigation is rigorous and conforms to ethical standards, and the methods are clear and well-described.
Validity of the findings: Validity of the findings: Findings are robust, conclusions are well-supported, and speculation is clearly identified and appropriate.
Additional comments: The manuscript describes a survey of potential bridge hosts (primarily songbirds and small mammals) to investigate the potential role these species might play in transmitting influenza A viruses from reservoir hosts to poultry. The survey is conducted in Iowa at several poultry and wetland sites during both fall and spring after a large poultry outbreak in the state.  Samples were tested for influenza A virus and antibodies and no positives were detected.

The manuscript is well-written and very clear throughout. The background information and discussion are very thorough and well documented.

I only have a single comment that I think should be addressed (and even it is relatively minor):
Line 311 - The authors used a cut-off of 0.6 rather than the manufacturer’s recommended cut-off of 0.5. While the higher threshold is appropriate (and supported by Brown et al. 2009, Clin. Vaccine Immunol. and Shriner et al. 2016, J Vir Methods), the authors use the manufacturer’s sensitivity and specificity values in their analysis of a seroprevalence range. Since the manufacturer’s sensitivity and specificity values are based on a cut-off of 0.5, I recommend that the authors should either apply a cut-off of 0.5 to match the manufacturer’s sensitivity and specificity values (this is the easiest solution since it won’t change results) or they should adopt the sensitivity and specificity values that match the 0.6 cut-off (found in the Brown et al. or Shriner et al. papers).

Minor comments
Line 55: The authors might consider replacing “epidemic” with “epizootic” throughout the manuscript.
Line 85: The authors might be a bit more clear about what they mean by “cyclical” in this sentence. In Ref. 35, I believe the cyclical nature of natural infections is associated with underlying immunity to a particular subtype whereas in Ref. 36, I believe the cyclical nature of infection discussed is the seasonal cycle of infection prevalence.
Line 103: I would quibble that this statement may be generally accurate in Iowa, but that natural ponds frequented by waterfowl are not uncommon on or near poultry facilities in other geographic areas (e.g., MN). Also, NPDES ponds attract waterfowl, even in Iowa.
Line 111: Recommend deleting the “of.”
Line 140: Recommend adding the word “a” before the word “given.”
Line 165: The authors might consider changing the “to” to “in.”
Line 181: Use consistent capitalization for bird common names. Consider adding scientific names at first occurrence of species in the text.
Line 216: I would suggest that variation is dependent on both species and viral strain.
Line 221: Did the micro centrifuge tubes contain an anticoagulant (i.e., EDTA or heparin)?
Line 367: The authors might consider noting that none of the APHIS/DNR positives for LPAIV occurred in counties where they sampled bridge hosts. Did any of the 3 APHIS/DNR negative counties overlap the counties where bridge host sampling occurred?
Line 387: Technically the IDEXX assay tests for influenza A specific antibodies and is not specific for avian viruses.
PeerJ does not include funders in the Acknowledgements 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: EVALUATING THE ROLE OF WILD SONGBIRDS OR RODENTS IN SPREADING AVIAN INFLUENZA VIRUS ACROSS AN AGRICULTURAL LANDSCAPE
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper is clear and the hypothesis is reasonable. I believe that the negative results are important. The background abstract and background for the study are appropriate. However, the material on surveillance in waterfowl appears as an afterthought. The reader is surprised when the section appears in the methods and the results are barely discussed. Either this section should be removed and the context of influenza prevalence in the areas surveyed are established through published literature. Or, properly describe and analyze the results from waterfolw. What subtypes were present? Were any of the samples isolated? Etc.
Experimental design: The design is fine. I think for the results to be truly conclusive longitudinal surveillance is necessary. But this does provide some important data that is relevant to influenza introductions to and spread among poultry populations.
Validity of the findings: no
Additional comments: After the high path outbreak was detected in farms a number of hypotheses were put forth 1) wild birds were spreading and introducing viruses to each farm experiencing outbreaks. 2) viruses were being spread by fomites. 3) viruses were being spread by other minor hosts such as small mammals and song birds. 4) viruses were being spread by humans passively (tools, workers, trucks etc). It's important that we have data so that we can reject those ideas that are not supported in order to properly identify transmission pathways and effective control measures. I am happy that this manuscript attempt to address some of the spurious or unlikely hypotheses. I recommend that the results about the surveillance in waterfowl be either removed or extended. These results are not treated appropriately, nor is their relevance to the rest of the results clear.


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: EVALUATING THE ROLE OF WILD SONGBIRDS OR RODENTS IN SPREADING AVIAN INFLUENZA VIRUS ACROSS AN AGRICULTURAL LANDSCAPE
Review round: 1
Reviewer: 3

Output:
Basic reporting: This study investigated the role of potential avian and rodent bridge hosts for Avian Influenza viruses (AIV) soon after the outbreak in poultry farms of HPAI H5N2 in 2015 in Iowa, United States. The study design focused on sampling these potential bridge hosts at both wetlands where the AIV reservoir occur (i.e. waterfowls) and at poultry farms where HPAI outbreak happened or could have happened. qPCR and serology diagnostics were implemented on both rodent and bird sampled with no positivity detected in the 449 animal sampled. A point to be noted is that mechanical transmission was investigated by swabbing the external body of animals sampled. The authors also compared the community composition of the samples from the wetland and farm sites to identify which species may be more involved in bridging wetland and farms from an epidemiological point of view.
In the discussion section, these negative results are discussed in relation to positive results found at the same time in waterfowls in the same state. The authors conclude that the species sampled may not be involved in transmitting AIV from waterfowl to poultry farms and that human induced transmission maybe more involved in farm-to-farm transmission.

The article is well written, hypotheses are well stated and tested. The literature references are up to date with the scientific field.

I appreciated the approach and the study design and have only minor comments about the study design and some points in the discussion that could be improved and/or further discussed.
Experimental design: - L162-170: site selection: the logic behind the site selection is not completely stated. You have 2 “pairs” of sites including a wetland and a poultry farm and other sites (wetlands and farms distant from each other). I guess there must be some constraints or other factors that drove site selection but they must be indicated. For example, why choosing the Malcom site outside any “coloured” cell? And why not in the single orange cell?

- L236-247: It is difficult to understand exactly if the waterfowl sampling is part of this study or not. You give a sample size and an AIV prevalence but little other information is available about the sample composition (in terms of species for example). If this information cannot be presented in this manuscript because it was collected by another team, I think this should be clearly stated and only the relevant information should be presented. If the information was collected by the authors, then more information should be given. Did those samples were pooled like the ones for the songbirds?

- L331-337: I think you need to state that you assume that the community sampled is representative of the bird/rodent community present. It is necessary because you make this assumption without stating it and without discussing it in the discussion section (see below).
Validity of the findings: The findings of the study are relevant for the field, well presented (see below a couple of suggestion for improvement) and will inform further AIV wild bird and rodent surveillance in the United States and beyond.

- Figure 1: Maybe use different symbols for wetland and poultry farm sites in order for readers to automatically detect them without referring to the text.

- Table 2: I think it is important to present at least the confidence interval of the prevalence estimation for each species (for the total of each species). Despite all your efforts, the sample size is often low for each species and therefore the confidence that AIV was not present in the species’ population is sometimes weak.
Additional comments: - L.70: but see also a recent publication: Caron et al. 2016 in Journal of Applied Ecology. This publication could be used elsewhere in the manuscript as well (“songbirds have been found to be capable of carrying AIV” – L105-106).

- L.106-108: in case you have not seen them and not to be cited at any cost (and sorry for self-citations but little has been done unfortunately on the topic) but consider also Caron et al. 2009 in Infection, Genetic and Evolution and Caron et al. 2010 in Ecology & Society looking at a conceptual approach and a more risk-based approach respectively to your study design.

- L407-417: I agree that you have identified “potential bridge species” within your sample that can connect wetland and poultry farm. But you should discuss at least 2 points. First, the scale of your study is larger than what I would call an ecosystem scale where you sample birds from adjacent wetlands and farms (a few kilometres). This is the case for two pairs of sites but you analyse your results globally across all sites. So maybe that species detected at one wetland were identical to species detected at a distant farm but not at a close farm. In fact, you assume homogenous distribution of species across your study site and should discuss it further. So the risk of AIV transmission from a wetland to a farm is maybe not “real” at all your sites. Second, you only take into consideration the community of your sample and not the “real” community present at site. This should be stated clearly. Capture techniques, time and season do not randomly sample within the bird community. There is a possibility that your potential bridge species (present and abundant at wetland and farm sites) are not the most abundant and shared species between wetland and farm sites within the “real” wild bird community.

- Given your approach, you still largely sample blindly within the bird/rodent communities. Estimating rodent community is difficult but bird communities can be characterised through bird counts. You should maybe mention that this could be a possibility to improve your protocol if time allows (which can be tricky in the case of an outbreak).

- In the discussion, you should also mention that your species sample size is low for most of the species sampled and therefore that the absence of AIV detection does not prove absence of circulation in those species. L449-452, you mention high sample sizes to reach good estimation of prevalence, but you should also say that at the species level, your sample size is often extremely low and cannot estimate much.
You rightly say that further sampling should target (capture techniques should be adapted) identified potential bridge species with the objective to achieve a better sample size. L413-417: you should specify that more targeted sampling could improve our understanding of some of the potential bridge species identified.

- Finally, in the last section of the discussion, you qualitatively assess the risk of spread of AIV from wildlife to poultry and vice-versa. Maybe you should also emphasize that an outbreak can be triggered by a rare event and then subsequently spread between poultry farms by farm-to-farm contacts. So AIV prevalence in bridge hosts, even if very low, represents a risk with potential high consequences.

- Conclusion: L478-480: can you really say this? I would say that your study did not detect AIV in potential bridge hosts and that it supports the hypothesis that they don’t play a role in AIV epidemiology in Iowa.


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: EVALUATING THE ROLE OF WILD SONGBIRDS OR RODENTS IN SPREADING AVIAN INFLUENZA VIRUS ACROSS AN AGRICULTURAL LANDSCAPE
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Great revision; I have no substantive comments or recommended changes; the following comments are meant for discussion only.

Line 214: I don’t think a change is needed, but want to point out that the Spackman et al. paper only compared BHI and PBS, neither with antibiotics which can be important, especially for cloacal/anal swabs which are likely to have strong bacterial communities. I know optimal is in the title of the paper, but this seems like an example of making inference beyond the data set, especially since your samples were not stored in an ultracold prior to shipping to the diagnostic lab.

Line 249: The “As with samples for small birds and mammals,” is a bit misleading because I think the APHIS surveillance uses 3mLs of BHI whereas you used 2mLs. You might just strike the beginning of the sentence or specify the 3mLs (assuming I’m correct about the 3mLs).

Line 277: if you were using an H5N9 isolate, you might mention that the extractions were conducted under enhanced BSL-2 or BSL-3 conditions/in a biosafety cabinet.

Line 285: AB?

Standardize capitalization of influenza: it is only capitalized in Lines 394, Table 3, and Line 411. Also there is a bit of inconsistency in references (some titles are capitalized, but most are not). Also, in Table 3, remove capitalization of Americana for redhead.

Line 415: Although I this is a unreasonable assumption, there are very scant data available on long-term AIV antibody persistence, especially for non-traditional hosts and a single infection. A potential difference between the studies you cite and your study is that geese are long-lived and are likely to have multiple exposures (resulting in an anamnestic response), even within a given year. Multiple exposures increase peak detectable antibody responses and the duration of the response so the 3-6 month estimates may be on the high side for the animals you are sampling.

Line 457 – A very minor point, but the 16% might be biased a bit high. I don’t know if you had access to the sample dates for the APHIS data you used, but the APHIS online data (across the US, not just IA, https://www.aphis.usda.gov/animal_health/downloads/animal_diseases/ai/monthlysummary.pdf) show much higher prevalence in August and September than the months during which you sampled so if you didn’t adjust the prevalence for the time period that overlapped your sampling, the 16% might be on the high side.

Line 496: seems like there might be a missing “to” in this sentence?


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: EVALUATING THE ROLE OF WILD SONGBIRDS OR RODENTS IN SPREADING AVIAN INFLUENZA VIRUS ACROSS AN AGRICULTURAL LANDSCAPE
Review round: 2
Reviewer: 2

Output:
Basic reporting: Introduction

- L61-63 : first sentence. The impression left by this sentence is that waterfowl are the culprit. Maybe adding something like “(…) can cross the wildlife-domestic animal interface and find optimal conditions to evolve towards higher pathogenicity in poultry production systems , sometimes (…)”.

- L86-87: “most poultry farms now enforce strict biosecurity protocols”: yes… in developed countries. Maybe contextualise here.

- L101-102: I don’t think this sentence is necessary there as you repeat it at the end of the introduction.
Experimental design: - L326-328: are these tests been developed for waterfowl? Are they species sensitive? You should maybe specify this.
Validity of the findings: - The fact that your confidence intervals don’t include zero is a problem for me. You should explain more the reason why, maybe in the M&M section. With only zero results, you cannot have confidence interval above zero, it is impossible within my logic. This could be an artefact of the Bayesian method but at the end I don’t see how all of your results have a non-including zero CI.

- The discussion has been improved taking into account the various pointed out in the previous revision.
Additional comments: Most of my previous comments/remarks have been addressed. I have only a few minor points to be a considered below. I believe the manuscript has reached the standard of 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: SHIFT OF SYMBIONT COMMUNITIES IN ACROPORA TENUIS JUVENILES UNDER HEAT STRESS
Review round: 1
Reviewer: 1

Output:
Basic reporting: 1.	The ms is clearly written. Literatures and background are well provided. Figures are acceptable.
Experimental design: Research question well defined and it is stated how this study fills an identified knowledge gap. Investigation performed to a high technical and ethical standard. Replicate should be described more clearly (see the general comments for the authors).
Validity of the findings: Data is robust, statistically sound, but probably small mistakes in description of the results (see the general comments for the authors).
Additional comments: 1.	The authors wrote in the Introduction that they studied changes in Symbiodinium communities associated with A. tenuis juveniles for the long-period of 1.5 years (line 97-98). But this is misleading, since actually most experiments finished in 2 or 4 months and only small numbers of juveniles survived up to 1.5 years.
2.	The authors described that the range of seawater temperature in tanks (the first paragraph of the Temperature treatment section). Do the values mean daily minimum and mean daily maximum temperatures ± SD for 2 tanks in 2012 and for 3 tanks in 2013? Please explain this more clearly.
3.	They compared prevalence of Symbiodinium types among temperature treatments. Is P=0.028 for D1-4 after 4 months not significant (line 251)? What is the level of significance used in this study? Is P=0.006 for A3 (0 day) not significant (line 259-262)? Please check.
4.	In 2012 experiment, there was a significant difference in the prevalence of the three Symbiodinium types among temperatures. Still the authors describe the changes of each Symbiodinium type at all temperature conditions together (line 243-248).
5.	In 2013 experiments, they found no significant effects of temperature conditions on the prevalence of Symbiodinium types. But they described changes in the prevalence of each type separately at each temperature (line 255-259). It is confusing. The meaning of the latter half of the sentence (line 257-259) is not clear.
6.	When they state that type C1 decreased under ambient and 32oC, but increased at 30oC (line 255-257), were there significant differences in the prevalence among different sampling time point?
7.	They used two tanks for each temperature condition in 2012 and three tanks in 2013 experiment. Do they use individual juvenile as statistical unit regardless of tanks? They described in the method section that 10-20 juveniles were sampled from each tank at each sampling point. But, if they show the number of replicates in the legend of Figs. 2, 3, and 4, it would be clearer.
8.	In the discussion, they state that the observation by Abrego et al. (2009) explains why none of the juveniles in this study harbored C3 Symbiodinium. But it is not clear why? Please make it clear. (line 378-380)
9.	They state that similar changes within the symbiont community were observed at higher temperature during later stages (line 366-369). But increase of A3 Symbiodinium as seen under the ambient conditions was not observed in high temperature conditions during later stages (Fig. 3). Please clarify this sentence.
10.	The authors stated that colonies harboring only D1-4 increased under ambient (60%) and 32oC (52%) conditions (line 280-282). Under ambient condition, the red bar (D1-4) appears to be about 30% at 2mo (Fig. 4b). Please check whether the sentence is correct.
11.	The readers might want to know whether bleaching occurred or not during the high temperature treatment.

Small errors
1.	Acropora longicyathus instead of longicythus (line 76)
2.	Citation of Yamashita et al. (2013)
3.	Line 372-375, some words are missing. ‘, which’ can be inserted after ‘Pacific’.
4.	Line 477-478. Reference source is not adequate.
5.	Change instead of ‘chenge’ (line488)
6.	Proceedings. Capitalize the first letter (line 541)


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: SHIFT OF SYMBIONT COMMUNITIES IN ACROPORA TENUIS JUVENILES UNDER HEAT STRESS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript titled “shift of symbiont communities in Acropora tennis juveniles under heat stress” by Yorifuji et al” deals with multiple symbiodinium type association in juvenile coral and how this influences their response to high temperature stress.
Authors have carried out the work using the coral A. tenuis, over a period of 2 spawning seasons, effectively repeating the experiment twice.

Specific comments

1. Basic reporting

A. I recommend the authors to check carefully the English again, I find few mistakes in grammar and usage but this can be easily solved.

B. In the introduction, where you introduce Symbiodinium types, please use the scientific names for Symbiodinium that have already been assigned one. For example, type D1a  Symbiodinium trenchii

C. Background review and references are sufficient

D. Figures are OK, raw data has been shared

E. I don't see any hypothesis so I cannot comment on that. But the manuscript is self-contained with relevant results
Experimental design: 2. Experimental design

The research presented is within the Aims and Scope of the journal

A. I have some difficulty in understanding the experimental design. it would be nice if authors can illustrate their experiment,

B. Why you think 31 ºC is stress temperature? From the value you provided for your ambient seawater temperature range, the highest is already 30.82, and 30.93. How long was this high temperature in the tanks, assuming it to be during summer months? was there any effect on those control juvniles during this time?

C. When you say 250-400 juveniles for each temperature conditions, does that mean that all your 2-3 independent tanks for each temperature had 250-400 nubbins? When i see the raw data, it becomes clear that you pick up random number of juveniles for each tile for each treatment to do the analysis. This is not explain in the main text very clearly

D. In your raw data, for growth and survivorship, you show for each temperature treatment there are 2 sets of 8 tiles from which you picked up certain number of individuals which amounts to more than 30 individuals for each. However, your Symbiodinium data does not have that many number of juveniles analysed for each treatment. Why so?

In the text, line 142, you say 10-20 individuals were collected randomly for the tiles in each tank…..i assume this number is collective sample form 8 tiles, if so, why your raw data shows more than 20 individuals?

E. Line 165 is not clear. Please rewrite it

3. Results

A. You say in 2012, the observation continued up to 1.5 years, however this does not appear in any of the figures. You do have raw data in the supplementary, why?

B. Your results show large difference between 2012 and 2013, why?

C. You used the same parental colonies for both the experiment. Response to temperature (ambient and 30 ºC is different between the years. Do you think this might be due to parental effect? I don’t know hoe about the cross between colonies and which colonies sperm fertilised which colonies egg? Paternal and maternal effect also influences the ability of larvae and juvenile to overcome stress.

Why do you think that the response you observe in juveniles is solely due to Symbiodinium? why not the host itself? irrespective of what Symbiodinium type is present

As you see from your results, there is large variation, especially in 2013, the variation is so big both in prevalence of Symbiodinium types and also D type id always there, so are other types.

D. How come there is no adult Symbiodinium type in juveniles? even at 1.5 years? If so, do you have any idea at what age the juveniles have Symbiodinium same as Adults? - in Okinawa, because as you mention in Discussion (line 375), it is by 1.5 years in the GBR.

D. D1-4 is outdated nomenclature for Symbiodinium. Please update.

Please see the recent publications by LaJeunesse group
Validity of the findings: This will be an important contributions in the field of Symbiodinium shuffling in early life stages of corals and how this might be related to the ability of juveniles to overcome stress. However, I do want to say that, the process of resistance in corals to stress is not solely dependent on the type/types of Symbiodinium it associates with. I feel that the authors opinion is biased towards Symbiodinium effect. Unless it is proven for sure that the Symbiodinium play the sole role in coral stress resistance mechanism, it is not fair to go in this direction.

I am not forcing authors to think in any direction, but may be try to be neutral and put forth both possibilities? there are many papers to support both aspects.

Even from the results of this work, one cannot conclude that Symbidinium shuffling as stress resistance mechanism. Because, the data is from random individuals collected out of hundreds. This might lead to underestimation since the percentage of types in each individual vary.

Also the death of juveniles through time could be due to natural process and finally very few survive and then you see certain Symbiodinium type to be dominant and think that the survival is due to the presence of such type/types, but this might not be the case.

Again from the data presented in this manuscript (line 275), in 2013 50-70% of juveniles at all temperature associated with A3 or C1 in the beginning and then S. trenchii increased under ambient and 32 ºC. This is good example of random changes.

Also when you say that (Line 285) “A greater proportion of coral colonies (this is “Juveniles” and not “colonies” right?) that harboured only S. trenchii survived under 31/32 ºC compared to other treatments”. How do you know this? every time you sampled, you sacrificed the juveniles, there was no way to monitor the type composition in the the juveniles throughout and in the end those survived had S. trenchii, but is it not possible that even those that died also could have been associated with S. trenchii?

So, the reason for increase in the proportion of S. trenchii at later stages of the experiment might have been due to increased mortality of juveniles harbouring different types of Symbiodinium including S. trenchii?
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: SHIFT OF SYMBIONT COMMUNITIES IN ACROPORA TENUIS JUVENILES UNDER HEAT STRESS
Review round: 1
Reviewer: 3

Output:
Basic reporting: This manuscript addresses the changes in symbiont communities in Acropora tenuis juveniles under heat stress, over a period of four months in one year, and over a period of two months in another year.  The study found the prevalence of Symbiodinium type D1-4 and the number of juveniles harboring this type to be higher under heat-stress conditions after 2-4 months.

The authors did a thorough search of the literature to provide a very detailed introduction and the methods were mostly clear and, again, very thorough in providing all the relevant information of how the experiment was set up and how analyses were conducted.  There are some spelling and grammatical errors throughout the manuscript, so careful review of the entire document would be necessary.
Experimental design: The experiment was rigorously done, though some continuity between the results in 2012 and 2013 would have been ideal.
Validity of the findings: Given that thorough DGGE analysis had been employed for this study, it would be important to show some a figure with DGGE gel pictures depicting the different patterns associated with the different Symbiodinium types, and which were found in which corals, under which temperature treatments and which time points.  Even showing a subset of these data would suffice to give readers an example what was analyzed and how different were the types.  The authors can then conveniently refer to this figure under 'Symbiont types in coral juveniles and adults' in the Results.  Given that clade F was dropped after this section, it would be informative to see what F looks like in a DGGE gel.

The terms "prevalence" and "occurrence" require careful explanation in both the text and the y-axis labels in the graphs.  At first glance of just the figures, it was unclear what was the difference between the two terms.  The y-axis labels would be clearer if changed to "Presence of symbiont type (%)" in Fig. 3 and "Proportion of juveniles (%)" in Fig. 4, or something of the like.  The clear distinction should be made in the Methods, Results, and Discussion as well.

Fig. 3a shows that type D1-4 is already the most stably prevalent throughout the 4 months at each temperature treatment in 2012 that it would seem difficult to make the case that it is more prevalent at the higher temperatures.  The authors can make this case in 2013, however, with the increased prevalence of type D1-4 at 32C in Fig. 3b.  But if this conclusion can only be drawn from one set of data but not the other, then there is the question of how repeatable this result is.  This would suggest that changes in symbiont communities occur naturally over time, and it is not very conclusive that it is indeed due to temperature alone.  The authors also allude to this in lines 331-333, and it is something to carefully consider.

Fig. 4 demonstrates a higher proportion of juveniles harboring type D1-4 at higher temperatures in both years, and some arrows indicating the bars of interest (4-month ambient vs. 4-month 31C in 2012, and 2-month ambient vs. 2-month 32C in 2013) would be helpful and easier for the reader to see.

Fig. 5 could be enhanced with labels of the Symbiodinium clades/types to the right of each shaded cluster.  At present, the reader would have to guess/assume that blue clusters to A, red to D, and green to C.

There seems to be some errors in the text where results reported do not match the depiction in the graphs.  For example, 63.2% in line 246 is not visible in Fig. 3a, and neither is 60% in line 281 for Fig. 4b.  Line 216 should also say Fig. 2a, not 2b.

While the study found the prevalence of Symbiodinium type D1-4 and the number of juveniles harboring this type to be higher under heat-stress conditions after 2-4 months, neither of these aspects seem to help the juveniles survive better or grow larger.  It is true that the juveniles that did survive after 2-4 months in 2012 seem to be dominated by type D1-4, but overall survivorship is consistently less than 20% at 2 months, 3 months, and 4 months (Fig. S2a).  In other words, survivorship did not improve when juveniles were harboring type D1-4.  Therefore, this cannot be considered any type of acclimatization, when these juveniles are clearly not doing so well, and survivorship at 31C is lower than at 30C or ambient temperature.  And the 2013 results (Fig. S2b) did not show any type of pattern at all.  Hence, it is huge leap to make the conclusion that "type D1-4 increases the heat tolerance of the juveniles" (Discussion, lines 350-351).  Additionally, the results at 1.5 years in the 30C treatment should be interpreted with caution, as there is no control treatment to compare that to.
Additional comments: Examining the potential to shift symbiont communities at the coral juvenile stage is important and currently understudied; hence, this attempt by the authors is appreciated and needed in the field.  However, the main concern for this manuscript is that the current results do not support the conclusion that clade D Symbiodinium benefit the survivorship of the juveniles under heat stress.  The results even slightly suggest the opposite.  Therefore, the authors can conclude that (1) type D1-4 is more prevalent in juveniles at the higher temperature in one year and that (2) it occurs in a larger proportion of juveniles at the higher temperature in both years, but that is it.  The question of how these two findings could benefit coral juvenile survivorship, growth, and overall health remains inconclusive.


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: INTROGRESSION BETWEEN ECOLOGICALLY DISTINCT SPECIES FOLLOWING INCREASED SALINITY IN THE COLORADO DELTA- WORLDWIDE IMPLICATIONS FOR IMPACTED ESTUARY DIVERSITY
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: In this paper, Lau and Jacobs report morphological and genetic data that clearly separate the northern Gulf of California sister species, Colpichthys regis and C. hubbsi, and provide evidence for introgressive hybridization between the two distinct species in the Delta region.  The paper was very well written and easy to follow.  Analyses and presentation of both morphological and genetic data were appropriate and quite thorough, and supported the authors' main conclusions.  I only have a couple of comments that I feel the authors might want to address.  Although seemingly trivial, the name "Scripps Institute of Oceanography" is not correct; "Institute" should be changed "Institution" in both the text and supplementary material.
     The second comment regards the bimodal distribution of the mismatch distribution of C. hubbsi (Fig. 4C).  Although the SSD and raggedness statistics were not significant, and the sudden expansion model could not be rejected for either species, these metrics are known to have low statistical power.  The mismatch plot of C. hubbsi would suggest a stable population.  It might be worthwhile emphasizing this a bit more (e.g. line 313), especially since the side-by-side plots of C. hubbsi and C. regis clearly show two distinct patterns, which are consistent with the two distinct haplotype networks.


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: INTROGRESSION BETWEEN ECOLOGICALLY DISTINCT SPECIES FOLLOWING INCREASED SALINITY IN THE COLORADO DELTA- WORLDWIDE IMPLICATIONS FOR IMPACTED ESTUARY DIVERSITY
Review round: 1
Reviewer: 2

Output:
Basic reporting: One relevant reference could be cited:  Hastings, P. A. & L. T. Findley.  2006.  Marine Fishes of the Biosphere Reserve, Northern Gulf of California.  Pp. 364-382.  In:  Felger, R. & W. Broyles (eds).  Dryborders: Great Natural Areas of the Gran Desierto and Upper Gulf of California.  Univ. Utah Press, Salt Lake City, Utah.

Otherwise, no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: This manuscript is well-written and data are thoroughly analyzed and conclusions are for the most part fully justified.  It represents an important contribution with relevance not only the system under study but also to similar estuarine systems around the world.
The attached pdf has a number of questions, mostly of clarification, suggested rewording, or request for supporting references.


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: INTROGRESSION BETWEEN ECOLOGICALLY DISTINCT SPECIES FOLLOWING INCREASED SALINITY IN THE COLORADO DELTA- WORLDWIDE IMPLICATIONS FOR IMPACTED ESTUARY DIVERSITY
Review round: 1
Reviewer: 3

Output:
Basic reporting: Meets all standards.
Experimental design: Meets all standards.
Validity of the findings: Meets all standards. Impact and novelty is well assessed.
Additional comments: This is a well conceived, written, and executed paper on an extremely important topic (the loss of estuarine habitat due to human water usage). It should be published as is (except a minor misspelling of Colpichthys in the abstract)


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: SUBSTITUTIONS INTO AMINO ACIDS THAT ARE PATHOGENIC IN HUMAN MITOCHONDRIAL PROTEINS ARE MORE FREQUENT IN LINEAGES CLOSELY RELATED TO HUMAN THAN IN DISTANT LINEAGES
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript demonstrates that alleles known to be pathogenic in humans arise more frequently in lineages closely related to humans.  The work laid out here is interesting, though I have a few concerns that I would like to see addressed. Overall, this manuscript is well written and I have included some minor suggestions to improve clarity in my line by line comments. The introduction and the discussion sections would benefit from further discussion of how this study compares to others. Please see the first of my general comments when addressing these comparisons.  Some of the figures can be hard to read due to the large phylogenies being shown. I suggest collapsing clades that do not contain relevant information. The work presented here appears to be self-contained and presents results relevant to addressing the hypotheses.

General comments

1.	The comparison of the findings reported here to published works demonstrating the occurrence of a mutation in one species is a predictor of its pathogenicity in humans may not be completely valid. From reviewing the cited literature, it appears that this observation is true for very closely related homologs. However, this observation may not be true at larger phylogenetic distances, such as those examined by the authors of this manuscript. It appears that the authors of this manuscript expected to find that human pathogenetic allele would be prevalent in distantly related species. Published results do not seem to suggest this hypothesis. Hence, claiming the results found in this study contradict previous works are not strictly valid because the authors examine much larger phylogenetic distances. I suggest that the authors add a further discussion about how their results differ from that of previous studies addressing differences in phylogenetic distances.

2.	Throughout the manuscript, it is suggested that the presence of an allele at a specific site is evidence of the allele’s fitness. The authors should review Kimura’s neutral theory of evolution and address that parallel or convergent evolution is not always indicative of fitness. Zou and Zhang (Mol Biol Evol. , 2015) shows that molecular convergence is often explainable by neutral models.

Specific Comments.

3.	The figures that include phylogenies are very hard to read, particularly Figure S9.  Consider collapsing clades where a change is not observed.

4.	Figure legend 1 claims that arrows are on the figure but none are present. The arrows are included in the supplemental figures but why the distance to flies is included is unclear.

5.	Include p-values in the text of the manuscript when you are claiming something is significantly different.

6.	Figure 7 does not include a y-axis label.
Experimental design: The research question is well defined, though a more detailed description the initial hypothesis should be given. Please see my first general comment when addressing this. The technical approaches used here appear to be appropriate. However, the methods section is brief and I would like to see the following questions I had about specific lines addressed.

Line 70: How did you constrain the phylogenetic trees?

Line 97: How was the binning of phylogenetic distances done? This really needs to be further explained because your results hinge on the size of these bins.

Line 102: How were these simulations done? Did you use a piece of software?

Line 136: Biased how?
Validity of the findings: Overall, I think the results of this project are sound. However, the manuscript itself needs a significant amount of rewriting. The methods section is brief and the results section does not place findings into a larger context. The authors should take care not to oversell their findings because I don’t think the comparisons to existing literature is valid.  If the authors feel that their findings are indeed comparable this needs to be carefully described, addressing differences in phylogenetic distances. Further, the authors need to avoid a selectionist view of molecular evolution. The presence of an allele at a site does not necessarily mean that it confers a fitness advantage, rather its presence may be due to neutral process.

The conclusion section of the manuscripts claims that

Line 240: a variant fixed in humans may be deleterious in non-human species. This was not demonstrated by this study.

The last paragraph from the discussion is just pasted into the conclusions section.
Additional comments: Minor line by line text comments.

Line 38:  Include SPFL after you introduce single-position fitness landscape directly after the term.

Line 42: Remove “than in distantly”

Line 52-55: The connection between two exponential distributions and the number of compensatory changes needs to be better explained.

Line 58-61: This is a run-on sentence, consider breaking it up for clarity.

Line 65: It is not clear if the 12 mitochondrial are also from Klink & Bazykin, 2007.

Line 74: Add a citation for the MITOMAP database.

Line 132: What is ‘it’ in the “…these species, it did not share…” sentence?

Line 147: Beyond just reporting thing fold change in phylogenetic distance include some context about what this result means.

Line 183: Change the word order to read “similar to normal human variations than to non-human variants”

Line 207 & 233: Add a sentence about what these differences in phylogenetic distances tells us.

Line 255: Equating phylogenetic clustering and fitness is a false claim.