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

Input:
Title: EFFECTS OF KNEE EXTENSION WITH DIFFERENT SPEEDS OF MOVEMENT ON MUSCLE AND CEREBRAL OXYGENATION
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors have presented a manuscript titled “Effects of knee extension with different speeds of movement on muscle and cerebral oxygenation.”  Eight female participants performed three sets of unilateral knee extensions at 50% 1RM with various velocities referred to by the authors as the amount of time provided for the complete of both concentric and eccentric motions of the exercise.  Frequency domain NIRS was used to assess deoxyhemoglobin, oxyhemoglobin, total hemoglobin, and oxygen saturation.  It is not clear from the abstract what muscle was analyzed and this should be clearly stated.  Both contralateral and ipsilateral prefrontal cortex (PFC) measurements were taken.  Authors stated that exercise at a slower speed increased deoxygenation of the muscle and the contralateral lobe of the PFC showed greater increases in oxygenation than the ipsilateral PFC.  The results presented by the authors is very intriguing yet there are several important areas that should be noted to improve the manuscript before acceptance.

The authors are suggested to consult resources available for the improvement of the English language used throughout the manuscript to better cater to the international audience of the journal.  It is also suggested that a native English speaking colleague to review the manuscript before submitting.  Some examples where language could be improved have been noted in the marked manuscript (Microsoft Word track changes) that has been included in this review.  Further grammatical and language corrections were not made for the rest of the manuscript which should be examined thoroughly by the authors before resubmission.

Formatting should be consistent throughout the manuscript. For instance, in the abstract authors state their hypotheses as numerals (i. and ii.; suggested to be 1 and 2; page 2) but then later at the end of the introduction the same hypotheses are listed as a. and b. For the hypotheses, they are vague in terms of outcomes.  The authors state they hypothesize that the changes will be higher but it should be stated clearly what that means (i.e. higher levels of oxygenation).
Experimental design: How did the authors confirm that the futsal players were not engaged in resistance training as part of their sport involvement? For the 1RM testing, what equipment was used? How was the predicted 1RM calculated? The authors state that only 30 seconds of rest was provided in between successive trials which is a very small amount of time for recovery during 1RM testing.  The National Strength and Conditioning Association recommends 2 minute rest intervals after the warm-up and 2 to 4 minute rest periods for the 1RM attempts (Essentials of Strength Training and Conditioning, 4th edition, Haff and Triplett).  Furthermore, research examining the rest interval length for 1RM squats states that at least a 1 minute rest interval, similar to that reported for bench press, is sufficient for recovery (Matuszak 2003).  It seems at the very least that a minimum of 1 minute with participant allowance to take further rest if requested would best ensure that a true 1RM was obtained.  The authors should explain their choice of 30 seconds for a rest interval and provide evidence that this is a sufficient rest period for producing valid 1RM loads.  The authors should describe their general protocol for 1RM testing.

What was the general range of motion achieved for the exercise? The authors state that full knee extension, noted as extended to 180 degrees or often referred to as 0 degrees of knee flexion, but what was the starting position for the lower limb?  Following 1RM, how were participants familiarized with the resistance exercise protocol?

For the exercise sessions, how was “concentric failure” defined?  Were there any allowable failed attempts and if so how many?  What occurred if participants were unable to keep pace with the metronome?  It was listed that exhaustion occurred during concentric failure but what if participants were successfully completing the concentric portion according to the metronome but were unable to properly control the eccentric portion of the movement?

It was stated that changes in NIRS variables were calculated as the difference between the absolute maximum variations from baseline but there was no explanation of how baseline levels were obtained.  Furthermore, the length of time to obtain maximum and baseline measurements was not stated.
Validity of the findings: The authors refer to the study by Tanimoto and Ishii who found that the longer duration of exercise movement resulted in increased deoxygenation but at the same time achieved levels of muscular size and strength to that of the faster movement duration.  The authors further state that Tanimoto and colleagues suggest that it is the large muscle deoxygenation that has a fundamental role in stimulating muscle hypertrophy but if this is the case, would the longer duration group who experienced the greater levels of deoxygenation not also experience greater strength and hypertrophy changes?  After analyzing the article, I am unable to see where those authors directly state how reaching a large muscle deoxygenation plays a fundamental role for muscle hypertrophy.  The authors need to better support their discussion about the importance of deoxyhemoglobin in relation to their remarks and be cautious of their interpretation of cited work. Additionally, in the conclusion section, the authors make a strong statement about lack of muscle oxygen having a key role in stimulating hypertrophy.  The authors need to better represent the current literature to make such statements. This occurs in lines 451-454 which also states, at least based on how it is written, that the current research linked lack of oxygen to hypertrophy which is not the case.
Additional comments: It should be noted that on line 363 that the study discussed did not use an elastic cuff but an inflatable cuff through the Hokanson system which is commonly used in blood flow restriction research.

Lines 185-186: This sentence is unclear as it is written and should be reworded.

Lines 190: Authors should properly define Fp point.

Lines 219 -222: Authors state the two factors (i.e. lobe and condition) twice in the same sentence for both ANOVA descriptions.  Only one instance is necessary.

Asterisks are misaligned in the figures making it more of a challenge to interpret.

The raw data has much information that is not included in the manuscript and further detail is needed to fully understanding the dataset.  For instance, it appears that standard jump, countermovement jump, MVC, and two isokinetic measurements were taken but none of these were discussed in the manuscript.  Columns X through AA have headings 30 m (s) and 60 (s) and it is unclear what these are referring to.  T0 and T1 are not defined.

Overall the authors have presented data that may improve upon our understanding of how contraction duration affects hemodynamics as measured by NIRS.  Although the data is interesting, the authors need to better support their discussion about the importance of their results and improve on the usage of the English language.  Furthermore, there is much lacking in the methods section for fully understanding the methods that were utilized and the authors should include greater detail in this area.  These changes should be made before acceptance is granted.


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

Input:
Title: EFFECTS OF KNEE EXTENSION WITH DIFFERENT SPEEDS OF MOVEMENT ON MUSCLE AND CEREBRAL OXYGENATION
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: The authors have made significant amendments to their original manuscript, and have addressed each of my prior concerns and questions. As such, I am happy to approve this article for publication.


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

Input:
Title: EFFECTS OF KNEE EXTENSION WITH DIFFERENT SPEEDS OF MOVEMENT ON MUSCLE AND CEREBRAL OXYGENATION
Review round: 2
Reviewer: 2

Output:
Basic reporting: NA
Experimental design: NA
Validity of the findings: NA
Additional comments: Overall, the authors appear to have addressed the concerns of the reviewers.  The attention to the concerns is greatly appreciated.  Before full publication, there are still some minor areas that should be addressed regarding grammar and formatting and data reporting.  The references are still not uniformly formatted (for example, some titles are all capitalized where some are not).   Please thoroughly check to make sure this is correct.  Furthermore, there are misspelled words found (for example, calliper).  I also did not see any of the data presented on the skinfold thickness in the manuscript or the raw data.  This would be helpful in the interpretation of data given the adiposity of the participants measured.  Figure 5A y-axis displays "HbB" but given previous reporting in the manuscript should be "Hb".  Figure 3 incorporates red and green colors which will make it challenging if not impossible for some readers that have color deficiency.


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: WHAT’S FOR DINNER? DIET AND POTENTIAL TROPHIC IMPACT OF AN INVASIVE ANURAN HOPLOBATRACHUS TIGERINUS ON THE ANDAMAN ARCHIPELAGO
Review round: 1
Reviewer: 1

Output:
Basic reporting: This interesting study surely deserves publication, since it deals with an anuran species that is not ranked among the widely recognized invasive amphibians, and hence it adds important information to the current knowledge about amphibian invasions. Moreover, the diets of two native anurans were summarized for the first time in the Andaman Islands, adding important information about the biology of these species. I suggest the inclusion of the word “potential” in the title (“…Diet and potential trophic impact…”) since no direct measure of negative impact (e.g. demographic change, survival rate) has been performed. Some statements by the authors in the discussion also concur with this interpretation (e.g. lines 288-289, 323). The language is good and professional, but some improvements could be made on some sentences (e.g., lines 85-90, 304-305, 320-321). The literature cited is sufficient, but I felt that a stronger background is required to support the second hypothesis investigated by the authors (see comments in the reviewed manuscript I have uploaded). The article structure conforms to the “standard sections”, although headings were not provided for the abstract. Figures are relevant, but I made some suggestions to improve their appearance and readability (see comments in the reviewed manuscript). The study contains results that are conclusive in relation to the two hypothesis stated; however, in my opinion the niche breadth analysis added no relevant information, since the temporal sampling was too limited to perform statistic comparisons, and the electivity and prey size investigations were sufficient in providing basis for the interpretation of niche overlap. Additionally, the authors poorly mentioned niche breadth in the discussion, so that I suggest this analysis to be removed from the study with no detrimental outcomes. Alternatively, in the case of maintaining this analysis a hypothesis about niche breadth should be stated, and a deeper discussion about niche breadth results ought to be included.
Experimental design: This study fits in the “Aims and Scope” of PeerJ, in both Biological and Environmental Sciences. The knowledge gap was clearly identified, and the research questions were well defined in the last paragraph of the introduction with sufficient background. However, the same is not true for the abstract, where a clearer statement of the research questions should be made. The authors provided an ethical approval statement, as well as the number of the capture permit (lines 135-138). The Methods were described in sufficient detail for most of the analyses; although some information should be added to clarify how recaptured frogs were considered during the estimation of prey frequencies (see my comment at line 154). Moreover, a correlative analysis designed to assess how prey size (volume) is related to frog size and to frog species should be included to better support part of the conclusions (see my comment at line 248).
Validity of the findings: I thank the authors for providing the raw dataset in a comprehensive format. Data are robust and statistically sound. Speculation was made, but well stated as such, on lines 263-268. The conclusions, however, need some improvements to be fully connected to the original questions, hypothesis and goals of the study (see my comments on lines 318-323). For example, no conclusive sentence has been done about predation behaviour, even though describing this behaviour was part of the aims of the study. Again, I ask the authors to perform a statistical analysis confronting prey size (volume) and frog size, accounting for interspecific effects (i.e., differences related to frog species), to better support the relationship between prey size and trophic niche overlap.
Additional comments: Further comments, suggestions and demands that I made can be found in the reviewed manuscript that I have added to this review. Pay special attention to the list of references; I found some disagreements between listed works and citations in the text (e.g., different years). I also recomend a revision in the literature cited to assure that all reference entries conform to the journal stile.


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: WHAT’S FOR DINNER? DIET AND POTENTIAL TROPHIC IMPACT OF AN INVASIVE ANURAN HOPLOBATRACHUS TIGERINUS ON THE ANDAMAN ARCHIPELAGO
Review round: 1
Reviewer: 2

Output:
Basic reporting: The whole manuscript is generally well written. However, the authors used several unpublished references throughout the whole text. Please check that whether it is allowed by the journal. In addition, the authors need provide more background knowledge on amphibian impacts and the specific study species here. Please see more detailed comment below in "General comments for the author" section.
Experimental design: The field sampling and survey is well done. However, the authors need more clarification on how they estimated the residence time of this frog invader in the study area. Please see my detailed comment below in the "General comments for the author" section.
Validity of the findings: Data and findings are robust. However, the authors need more clarifications on why they excluded the vertebrate preys from the diet preference analyses. Please see my detailed comment below in the "General comments for the author" section.
Additional comments: This work is very interesting since the authors focused on the diet composition and prey selection of the invasive Indian bullfrog in the Andaman archipelago, which is one global biodiversity hotspot. Compared with many researches investigating diet of the other invasive amphibians such as the American bullfrog across the globe, we still understand so little about the predation impact of the Indian bullfrog. Here, the authors found that this invasive frog in the Andaman archipelago can predate on native endemic vertebrates, and there is a high diet overlap of this invader with native Limnonectes spp., indicating its potential diet competition with native frogs. The authors further identified some preferred invertebrate preys of the Indian bullfrog after accounting for the prey availability in environment. The results of the present study are somewhat novel for this species and have important implications for conservation of native species in the Andaman Islands. The whole manuscript is generally well written. Following are my concerns, which may be helpful to the improvement of the manuscript.

Line 38-46, the descriptions on impacts of invasive amphibians need more details to increase readability of this work. For example, except for predation and competition, which are two most direct impacts on native species, invasive amphibians can also have evolution impacts on native frogs through reproductive interference (e.g. D’Amore et al. 2009, Theis & Caldart 2015) and transmission of amphibian diseases such as the notorious Chytrid fungus Bd (e.g., Garner et al. 2006, Liu et al. 2013).

Line 44, for documented predation impact on amphibians, please see also Liu et al. 2015, which provides direct evidence on the preference of the invasive American bullfrog on Chinese endemic frogs after accounting for the availability of different prey species in the environment.

Line 62-63, how about the impacts of Indian bullfrog on native amphibians in Madagascar, Maldives and Laccadive Islands? Are there more background knowledge on this invasive species?

Line 125: the authors need provide more detailed information on how they estimated the residence time (e.g., at least 3 years here) of the bullfrogs established in the two study sites. In addition, the authors need to give more information on the introduction or invasion history of this species in the study area.

Line 168: the authors need more explanations on why you excluded the vertebrate prey species from the diet selectivity analyses. In my opinion, the predation of bullfrogs on native vertebrates such as native frogs are very important for the evaluation of bullfrog impacts on native biodiversity especially the authors found that small vertebrates consisted a majority of the bullfrog diet in the study site. In addition, vertebrate preys can greatly influence the predation choice of the invasive bullfrogs on native species because vertebrates generally have higher biomass than invertebrates.

Suggested references

D’Amore et al. Reproductive interference by an invasive species: an evolutionary trap. Herpetological Conservation and Biology 4.3 (2009): 325-330.
Garner et al. The emerging amphibian pathogen Batrachochytrium dendrobatidis globally infects introduced populations of the North American bullfrog, Rana catesbeiana. Biology letters 2.3 (2006): 455-459.
Liu et al. Climate, vegetation, introduced hosts and trade shape a global wildlife pandemic. Proc. R. Soc. B 280.1753 (2013): 20122506.
Liu et al. Diet and prey selection of the Invasive American bullfrog (Lithobates catesbeianus) in southwestern China. Asian herpetological research 6 (2015): 34-44.
Theis & Caldart. Multiple interspecific amplexus between a male of the invasive Bullfrog Lithobates catesbeianus (Ranidae) and two males of the Cururu toad Rhinella icterica (Bufonidae). Herpetology Notes8 (2015): 449-451.


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: WHAT’S FOR DINNER? DIET AND POTENTIAL TROPHIC IMPACT OF AN INVASIVE ANURAN HOPLOBATRACHUS TIGERINUS ON THE ANDAMAN ARCHIPELAGO
Review round: 2
Reviewer: 1

Output:
Basic reporting: My original positive comments about the manuscript are still valid here. The manuscript was much improved over the original draft, which indicates the authors worked thoroughly to accommodate the reviewers’ suggestions and constructive criticisms. Almost all of my suggestions have been addressed and my questions answered. However, the position of the authors about the niche breadth analysis remains unclear to me. They removed the original figure about niche breadth and mentioned in the response letter that they had removed this analysis from the text. Nevertheless, I found mention to niche breadth in the Material and Methods (lines 201-206) and Results (line 233), where they just stated “Niche breadth (J’) was highest for Limnonectes, followed by H. tigerinus, and Fejervarya”, with no quantitative data. In contrast, niche breadth was removed from the Abstract and Discussion. I maintain my suggestion to remove niche breadth from the text, particularly now when the authors decreased the emphasis given to it in this revised version of the manuscript. Please see additional comments below in "General comments for the author" section.
Experimental design: In the response letter, the authors answered my question about how they had dealt with recaptured frogs; they had 54 recaptures and considered recaptured individuals as independent samples (this is my interpretation of their response; my apologies if it is not correct). I think they should add this information to Material and Methods (lines 166-168), or place it in the Results.
Validity of the findings: The conclusions of the study are now much more informative and aligned with the hypothesis and research purposes, reinforcing the validity of the findings.
Additional comments: -line 26: remove “the genus” before Fejervarya; in my opinion it is not necessary;
-line 165: word “length” is repeated;
-line 241: remove the signal “<” before 10 mm3;
-line 255: I expected to see more details about the two predation events of anurans by Limnonectes informed in this line; for example, the identities of the preyed species and the dates of recording. I think this sentence is of poor value in the current format, so please provide more information.


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

Input:
Title: WHAT’S FOR DINNER? DIET AND POTENTIAL TROPHIC IMPACT OF AN INVASIVE ANURAN HOPLOBATRACHUS TIGERINUS ON THE ANDAMAN ARCHIPELAGO
Review round: 2
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The authors have addressed all the comments from my first round of review. As previously stated, I think this manuscript covers an interesting and important topic in amphibian invasion ecology, that deserves publication in this Journal. I recommend this article for publication.


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

Input:
Title: OSTEOLOGY OF A FORELIMB OF AN AETOSAUR STAGONOLEPIS OLENKAE (ARCHOSAURIA: PSEUDOSUCHIA: AETOSAURIA) FROM THE KRASIEJÓW LOCALITY IN POLAND AND ITS PROBABLE ADAPTATIONS FOR A SCRATCH-DIGGING BEHAVIOR
Review round: 1
Reviewer: 1

Output:
Basic reporting: Manuscript is very well written for an author for whom English is not their first language; however, there are still quite a few grammatical errors that I have made suggestions for correcting throughout the text. The background materials are sufficient and literature references appropriate. The article is well-figured and has a good amount of useful supplemental material.
Experimental design: This is not the first time digging has been proposed for aetosaurs, but this is the most thorough treatment of that hypothesis to date. The hypothesis is well supported and discussion is clear. Methods are sufficiently described including in the supplemental materials. I have no suggested improvements.
Validity of the findings: The data are robust and conclusions well stated. I have no suggested improvements.
Additional comments: This is a well designed study and a well organized and written manuscript. There are some grammatical errors that need to be corrected.


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: OSTEOLOGY OF A FORELIMB OF AN AETOSAUR STAGONOLEPIS OLENKAE (ARCHOSAURIA: PSEUDOSUCHIA: AETOSAURIA) FROM THE KRASIEJÓW LOCALITY IN POLAND AND ITS PROBABLE ADAPTATIONS FOR A SCRATCH-DIGGING BEHAVIOR
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article is quite well-written and easily understood. It would benefit from some editing by a native English speaker, but otherwise there are few problems.

Generally speaking the references are adequate, although I think Long and Murry (1995) should be cited more often and Long and Ballew (1985) would also be good to include.

Personally, I would like to see a Figure 1 with a map and generalized stratigraphic understanding of the locality—I just think it's always good to try to provide geographic and geologic context of the fossils, even if that's not the primary thrust of the paper.

Although the figures themselves are well-executed, they would benefit if they were subdivided (e.g., Fig. 1A, 1B, !C) and if the author would take advantage of that, as it is sometimes difficult to decide which figure to look at to see specific morphology described in the text. I'm also not convinced that the figures are cited consecutively (e.g., Fig. 1 is the first figure called out).
Experimental design: This paper is straightforward and thorough, basically, I think that the scientific content is sound and well worth publishing. All of the criteria Peer J lists for this section (original, well-defined, relevant, rigorous, replicable) are satisfied.
Validity of the findings: I believe the author has adequately documented their work and I think that their findings are valid. I do think that it may be beneficial to cite a reference or two regarding things such as the presence of keratin inferred from bone texture (more than just "personal observation) as there's certainly literature out there.
Additional comments: Overall this was an easy paper to review, and I think it should be published with minor revision. Other than my previous comments on the figures, the only major problem is that there are parts of 3 different sentences (none complete) on line 569.

I do think that a close reading by a native English speaker/editor will take the text from "very good" to "excellent." I am traveling so cannot easily scan my copy of the manuscript, but I will try to find a way to send it to the editors.

Obviously I'm biased, but I think Heckert et al. (2010) should be cited on line 32 and Heckert and Lucas (2000) on lines 36, 92, and 595.

Long and Murry (1995) should be cited on line 83, 595, 608

260—"figure 8"-shaped, perhaps?

271—concaves is not a word, a different word is needed there.

line 595 should include citations of Long and Ballew (1985)

Line 898—italicize _Desmatosuchus_

My copy of Supplementary Figure 12 includes many typos in the captions (mostly missing spaces between words). Also, the correct attribution of species for _Longosuchus_ is _Longosuchus meadei_ (Sawin) 1947, as Sawin named the species, which was reassigned to the new genus _Longosuchus_ by Hunt and Lucas (1990).

Although the limbs are incomplete, the author  may want to look at the small aetosaur _Coahomasuchus_. I think that _C. chathamensis_ (Heckert et al., 2017) has enough preserved to at least see what the ratio of the ulna-radius to the humerus is.

Heckert, A. B., Fraser, N. C., and Schneider, V. P., 2017, A new species of Coahomasuchus (Archosauria: Aetosauria) from the Upper Triassic Pekin Formation, Deep River Basin, North Carolina: Journal of Paleontology, v. 91, no. 1, p. 162-178.

See also: Heckert, A.B., and Lucas, S.G., A new aetosaur (Archosauria:Crurotarsi) from the Upper Triassic of Texas and the phylogeny of aetosaurs. Journal of Vertebrate Paleontology, v. 19, p. 50-68. http://www.jstor.org/stable/4523969


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: PERIWINKLE CLIMBING RESPONSE TO WATER- AND AIRBONE PREDATOR CHEMICAL CUES MAY DEPEND ON HOME-MARSH GEOGRAPHY
Review round: 1
Reviewer: 1

Output:
Basic reporting: The introduction could use some reorganizing and there are a few minor grammatical errors (See specific comments attached).
Experimental design: Many more methods details are necessary and I am concerned that the experimental design does not test for differences between airborne and waterborne cues but instead tests for differences in the concentration of airborne cues. Authors either need to revise manuscript to reflect this, provide methodological/observational details demonstrating that snails are actually responding to waterborne cues, or redo the experiment using a revised design (See specific comments attached).
Validity of the findings: Looking over the raw data the authors should have enough samples to test their hypotheses. The figures indicate that there are major differences between treatments and snail populations although revised statistical analyses are necessary. Conclusions are well stated and linked to original research question. However, some of the authors' conclusions on why snails exhibited different behaviors across geographical location need to be better identified as speculation given the experimental design and available data (See specific comments attached).
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: PERIWINKLE CLIMBING RESPONSE TO WATER- AND AIRBONE PREDATOR CHEMICAL CUES MAY DEPEND ON HOME-MARSH GEOGRAPHY
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors satisfactorily meet the standards of PeerJ
Experimental design: I have three concerns about the experimental design.

First, in both experiments, the LA and NC snails were exposed to NC crabs. Consequently, it is possible that the LA snails climbed higher than the NC snails because the LA snails were perhaps less familiar (and thus were more alarmed by) the water and air-borne cues of the NC blue crab. I understand that it would have been difficult to transport LA crabs to the laboratory in NC, therefore logistics likely contributed to the experimental design. But this is still a flaw in the design and interpretation of the experiment.

Second, the factorial nature of the second experiment is not appropriate. Based on my interpretation of the methods, the authors used tanks as the experimental unit. They randomly assigned tanks among the three cue treatments. However, they didn’t randomly assign tanks among the two levels of the snail factor (population/origin). Instead, they put both snail populations in the experimental unit. As a result, the two different populations represent two different response variables, not two different levels of an explanatory/independent factor.

Third, and I feel awful for bringing this up, but the authors collected snails form only one site in the high latitude and one site in the low latitude. Thus, it’s unclear if differences between the two populations is random or real. I think the authors should have collected snails from a few populations in the low and high latitude areas.

A few minor questions/comments:

Line 38: do you mean “evolved” instead of “involved”?

Line 60: melongena is the crown conch, not horse conch

What is the rationale for mixed population experiment? A rationale for this general topic (not snail specific) should be developed in the Introduction of the paper.

End of review
Validity of the findings: The findings have alternative explanations due to experimental design (see points 1-3 above). However, the authors conclusions are not unreasonable.
Additional comments: Manuscript 24555v1 “Periwinkle climbing response to predator chemical cues depends on home-marsh geography” submitted by Carroll et al. represents two laboratory experiments there were designed to test whether snails from a low latitude origin (LA) display stronger predator avoidance behavior compared to snails from a higher latitude origin (NC), presumably because predation pressure is higher at the lower latitude location.

The text is clearly written and the figures are simple as well as easy to interpret. In short, I enjoyed reading the manuscript and I appreciate the author’s efforts.


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: PERIWINKLE CLIMBING RESPONSE TO WATER- AND AIRBONE PREDATOR CHEMICAL CUES MAY DEPEND ON HOME-MARSH GEOGRAPHY
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have provided better context and background. The English is professional although there are a number of minor errors throughout the work. See annotated PDF.
Experimental design: Research question is well defined. The authors do a much better job highlighting and clarifying the limitations of their experimental design and discussing their results. Some minor method details still need to be added. See annotated PDF.
Validity of the findings: The statistical analyses needs to be slightly revised before publication. Speculation is better identified. See annotated PDF.
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: PERIWINKLE CLIMBING RESPONSE TO WATER- AND AIRBONE PREDATOR CHEMICAL CUES MAY DEPEND ON HOME-MARSH GEOGRAPHY
Review round: 2
Reviewer: 2

Output:
Basic reporting: The revised article is clear with sufficient background, figures and tables. The results are also relevant to the proposed research questions.
Experimental design: The revised draft addressed my criticism of their statistical analysis of the second experiment.
Validity of the findings: In the Discussion, I think it needs to be clearer that the significant differences among control and cue treatments did not manifest until the two snail populations were mixed.
Additional comments: The paper is about geographic origin of prey and multiple cues. I suggest modifying the title to reflect the multiple cue aspect.

At approximately line  70, the Introduction needs to highlight study from Brian Helmuth lab that demonstrated snail climbing is also due to wind speed, humidity, and temperature.

The idea of mixing populations and its relationship to the overall research connections needs a little more development. Intraspecific (trait) variation is a pretty popular research focus right now. I suggest highlighting this more.

End of review


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

Input:
Title: AGE, BUT NOT SHORT-TERM INTENSIVE SWIMMING, AFFECTS CHONDROCYTE TURNOVER IN ZEBRAFISH VERTEBRAL CARTILAGE
Review round: 1
Reviewer: 1

Output:
Basic reporting: While the manuscript is well written overall, the text needs to undergo some language editing.
One consistent error involves the tenses used: the results are reported in the past tense, but often so are the conclusions drawn; in my opinion the conclusions should be in the present tense. For example, in the 6th sentence in the abstract, the text should be 'Our results indicate…' and not 'Our results indicated…'.
There are also other errors of syntax, for instance, in the first line of the paper (Introduction section) "…the most common arthritis…"-  a different term should be used, perhaps something like "…the most common pathologic condition of articular cartilage …", or a similar term.

The references are adequate, and so is the structure.

The introduction is clear

The relevance of the results and the conclusions drawn from these results are flawed in parts of the manuscript (see below)
Experimental design: As far as I can tell, the research is within the aims and scope of this journal

The research question is somewhat vaguely defined.

The investigation is adequate in terms of most of the techniques used

Some of the methods (like microCT, BMD determination) are not described in sufficient detail, or are not sufficiently clear
Validity of the findings: The authors are trying to establish a model for mammalian articular cartilage by studying the cartilage present in zebrafish cranial vertebra, but have not established the validity of this analogy: cartilage is present only in small areas in most ZF vertebrae, and the cartilage in the Weberian vertebrae seems very different from mammalian articular cartilage in terms of function and structure.

Intense swimming applies heavy loads mostly to the caudal vertebrae of fish, and therefore the pre-caudal vertebrae (particularly the Weberian vertebrae) are probably not the appropriate model for evaluating the effect of mechanical loading.

It is not sufficiently clear how the authors determined the BMD of the vertebrae of the ZF: the resolution of the scan (9 microns) does not seem adequate for this objective, and relevant scan parameter are not provided (rotation step, exposure time, etc.). Furthermore, the results are very low values compared to values reported in the literature (and in my personal experience).

I find the reported result, of significantly increased BMD and body length after 2 weeks of rest (the control group) extremely surprising, and the reliability of these findings must be better supported. In my experience, BMD values do not change significantly within a 2-week period.

The change in length after exercise is not explained well: does this have to do with the effect on the cartilage? Or more likely: an error of measurement or creation of spinal curvature?

Based on Figure 1 F, G, U and J, the control and exercise groups were not similar at the start of the swimming experiment, in terms of weight and body length, so comparisons may be difficult to make.

Line 235-237: I am not clear as to how the authors reached these conclusions.
Additional comments: No additional comments


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

Input:
Title: AGE, BUT NOT SHORT-TERM INTENSIVE SWIMMING, AFFECTS CHONDROCYTE TURNOVER IN ZEBRAFISH VERTEBRAL CARTILAGE
Review round: 1
Reviewer: 2

Output:
Basic reporting: Generally the manuscript is well written. There are, however, a few typos in the manuscript which need rectifying; these include one on line 375 (currently reads cartialge).

Given that exercise will impact muscle and as muscle is such a substantial component of the zebrafish trunk (and likely the largest determinant of mass) the manuscript could do with some comment on the likely impact of exercise on muscle and some background literature on this.
Experimental design: Could the authors clarify what they mean by fish for 4 and 12 month experiments being being purchased while the others were acquired?  As the fish came from different sources are their genetic backgrounds known and comparable between the groups? Fish of different genotypes and/or those raised differently are likely to have more variation between them than the effects from the exercise itself.

When discussing the effects of exercise are comparisons being made to fish from the same source, if not why not?

It was unclear to me whether weights of the same fish were taken before and after training if so then the specific increase and decreases of weight per fish would be better to present - if not why not? How is it known that the experimental group of would have had the same distribution (or length/weights) as the control group .

More  detail should be given to the experiment set up for exercise. It states that maximal resisting swim speeds were identified, but it is unclear what speed the fish were subjected to for the 8 hour regime. Surely not 100% of maximal speed as this is the speed at which they hit the net, but if not then what percentage? Or what speed. While calculating the max speed for each fish is admirable if each fish was swum at a different speed it makes direct comparison between individuals difficult and more detail on the experimental design is needed to assess the validity of the conclusions.

What was the stock density at which the fish were raised? Stock density as well as age can have a significant impact on body length and and even bigger one on weight (fish stocked at low density are generally fatter).

The body length decreases seem  surprising in a short period  - can the authors comment of what they think is occurring - loss of intervertebral distance or contraction of the muscles? Are these comparisons between the same fish (i.e. each fish measured before and after exercise)? What do the authors think would happen if the fish were then allowed to continue without exercise - would the fish regain their length or remain shorter?
Validity of the findings: Most of my points relate to the experimental design above, without more detail on the exercise regime and the source of the fish it is hard to judge the validity of many of the findings as it is somewhat unclear what is being compared.

For example how is it the case that in Fig.  1H exercised fish are heavier than controls, yet, in Fig 1J they have lost mass? This doesn't appear to make sense.

For example are the 12 month control and exercised fish the same ones measured and weighed at 4 months, if not why not?
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: AGE, BUT NOT SHORT-TERM INTENSIVE SWIMMING, AFFECTS CHONDROCYTE TURNOVER IN ZEBRAFISH VERTEBRAL CARTILAGE
Review round: 2
Reviewer: 1

Output:
Basic reporting: The article meets the listed standards
Experimental design: The paper describes original research, the research question is well defined and relevant.

I still have concerns about a few of the measurements reported in this manuscript, particularly the validity of process of BMD determination (the explanations provided in the rebuttal are in my opinion incomplete), and the values reported are very low for mature ZF.

BMD determination with a lab-source microCT are tricky, and the authors must provide more information: the images must contain scale bars (missing in Figure 2), explain how many slices were included in each VOI, how they confirmed that the equivalent VOI was examined for each fish, how was the partial volume effect avoided, was the scan done 180 or 360 degrees, etc. I would prefer to see in Figure 2 raw data rather than a heat map with no scale.

The other issue is the measurement of total length, and the surprising shortening of trained fish. Can the authors supply the images measured, and indicate the measurement on these images?
Validity of the findings: I am not convinced that a statistically- significant increase in BMD after a 2-week training period is valid, or that such a training period is likely to result in decrease in body length. Naturally my doubts are irrelevant if these findings can be rigorously supported, but I do not feel this was accomplished here.
Additional comments: I recognize the efforts and work done by the authors, and I think that the questions this study evaluates are relevant and interesting. I think that the paper is generally well written, and much data is provided. Certainly data on the impact of aging on the skeleton are  adequately documented.

However I cannot support publication of these unexpected results of the effect of a mere 2-week training   on BMD and total body length without more convincing validation.


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: AGE, BUT NOT SHORT-TERM INTENSIVE SWIMMING, AFFECTS CHONDROCYTE TURNOVER IN ZEBRAFISH VERTEBRAL CARTILAGE
Review round: 3
Reviewer: 1

Output:
Basic reporting: OK
Experimental design: Still the BMD measurements are not convincing, calibration is not described, Figure 2 A, 2B do not show the color scale.

Length measurements are also not rigorous.
Validity of the findings: I still feel I am not entirely convinced the findings of BMD and lenth changes after swimming are entirely valid
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: CAN SECONDARY CONTACT FOLLOWING RANGE EXPANSION BE DISTINGUISHED FROM BARRIERS TO GENE FLOW?
Review round: 1
Reviewer: 1

Output:
Basic reporting: The writing is generally clear, and the recent literature is referenced well. However, this issue goes back to (at least) the 1980s, and though Endler & Barton and Hewitt are cited, the basic arguments there about how secondary contact can be distinguished from primary are not explained.

The simulation results are given as figures; it is not clear how far the tables of results will be made available.

Sokal's (PNAS) work on "wombling" as a way to detect coincident divergence at multiple loci should be cited.
Experimental design: See below
Validity of the findings: The results are based on coalescent simulations, scaled with deme size, N. It is not at all clear how they  relate to actual populations.  In particular, LD is measured between "unlinked" sequences - but this is not equivalent to sampling unlinked genes in an actual population, because the recombination rate scales with N in the coalescent framework.  As stated, these "unlinked" sequences should be uncorrelated in the coalescent limit, but would not be in a real population.

There is no consideration of sample size - a fixed # of sequences is used.  This makes it hard to draw conclusions about statistcial power.

Bray et al's method is dubious because LD depends on allele frequencies, so that a correlation between dp and LD may occur without admixture.
Additional comments: Bertl & Blum use coalescent simulations of a one-dimensional chain of demes to investigate whether various statistics can distinguish secondary contact from isolation by distance in the presence of a barrier to gene flow.  This is a long-standing and important question, which is now getting increased attention with the availability of extensive genetic data.  However, the treatment is very limited, and is not related to exisiting theory.  A thorough examiniation of these issues would be welcome, but this paper ius very far from that.

The various statistics are nit defined in the paper, so one has to go back to the original papers.  Actually, these statistics are closely related - for example, Fst as a function of distance is another way to represent spatial autocorrleation of allele frequencies. These relations would be clearer if the definitions were set out using a common notation.

Most data come from two-dimensional populations over a very large range, relative to local dispersal.  It is well known that both range size and dimension have strong effects on genetic differentiation.  Thus, these results could be misleading if compared with actiual data.

The effects of isolation by distance and of a barrier to gene flow in one and two dimensions are well-known theoretically, and the simulation results need to be compared with these - if only as a check that the simulations are correct.  In fatc, comparison with theory would allow a much deeper understanding of how these statistics depend on the parameters than these limited simulations. Indeed, it woiuld become apparent that dimension and range size are curcial, as noted above.

Secondary contact generates a transient  local increase in diversity and in LD, though a barrier will also generate a similar effect, albeit generally weaker.  A basic starting point should be to explain the theoretcial expectation for how these quantities behave following secondary contact or in a stationary IBD model, and how this is expected to be reflected in the various statistics.

It needs to be made clear at the outset that the paper only deals with neutral processes, and that the barrier to gene flow is a purely physical barrier.  GIven that there is much discussion of the effects of genetic barriers, there is scope for confusion here.


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: CAN SECONDARY CONTACT FOLLOWING RANGE EXPANSION BE DISTINGUISHED FROM BARRIERS TO GENE FLOW?
Review round: 1
Reviewer: 2

Output:
Basic reporting: I think this is a solid paper, clearly written and self-contained that would be of great interest  to population geneticists.

I thank the authors for their effort to provide the simulated data (ms commands, simulation outputs) together with a detailed README file, both accessible on the Figshare repository.   However, there is no explicit note in the main text indicating that the raw data is being deposited on Figshare, and the corresponding URL is also missing.

I have few minor comments:

• L87 – 89: Please give more details of why the development of LocalDiff questioned the possibility to discriminate between the two models.

• L463: Please replace “mutation rate” by “migration rate” in supplementary section 6.

• Fig1 and Fig2: Please consider giving the definition of the different parameters in the caption, so the readers can understand the figures without having to come back to the main text. Also, could you indicate directly on the schemes the different zones you define later (i.e., “centre”, “edges” and “range”)? It will help readers to visualize them.

• Fig3: Could you give in the caption the actual values used in the main simulations for all parameters (deme size, migration rate, time of split, expansion speed and bottleneck intensity)?

• Fig3 and FigS3: In the caption, does “Here, center denotes” refers to the FST plot?

• FigS6: Please consider changing purple with another, more distinct, color.
Experimental design: A key strength of this paper is in the rigour of the analysis, and I only have few suggestions.

2.1. I really appreciate that the authors explicitly accounted for space in the secondary contact model, both during range expansion and in the suture zone, as it is usually neglected in the speciation literature. However, I was somehow frustrated to see the analysis of a model of secondary contact with barrier to gene-flow relegated to the supplementary information (FigS6) and shortly commented in the discussion (L258 – 264). It has long been known that hybrid zone maintained by strong linkage disequilibrium among genetic incompatibilities are not stabilized geographically. They are expected to move until they reach a geographical barrier to dispersal (Barton 1979), a local region of low abundance (Nagylaki 1976) or an ecological boundary (Bierne et al. 2011). So secondary contacts usually coincide with regions of reduced gene-flow that maintain reproductive isolation. I think this should deserve more attention. Please consider clarifying the introduction starting from L45, and perhaps moving FigS6 in the main text.

2.2. It could be surprising to think about secondary contacts as converging to a migration-drift equilibrium (L45–48). The authors should distinguish between neutral loci and selected loci  involved in reproductive isolation when saying that “secondary contact is a non-equilibrium situation that converges to a migration-drift equilibrium”. Neutral loci in a secondary contact model can quickly lose their initial association with the selected loci, and, indeed, converge to a migration-drift equilibrium. The genetic structure at neutral loci will depend on the geographic connectivity at a large scale, and can create isolation-by-distance patterns (Bierne 2013). On the contrary, the “speciation” loci are under selection-migration balance, and they are expected to decrease the effective migration rate of linked neutral loci (Barton 1979). It would be worth mentioning the distinction between selected and neutral loci in the introduction given that their molecular pattern are expected to be different.

2.3. Table 1 gives the results of the test for admixture (the null hypothesis being no admixture) in the case of secondary contact and isolation-by-distance. The authors have assessed the robustness of the test to varying times since secondary contact and varying intensities of the barrier to gene-flow. I would like to see how the power of the test (reject no admixture when there is admixture) and the false-positive rate (inferring admixture when there is isolation-by-distance) depends on varying the number of SNPs sampled? Also, what is the robustness of the test to varying level of migration rates in the secondary contact model? The authors may consider presenting these additional analyses in supplementary tables.

2.4. Since the primary goal of the paper is to discriminate between the two models based on a set of statistics, I think the authors should give some practical hints to readers who may be interested in applying the method to their study system. In particular, the directionality index seems promising.

Referring to lines 76–77, I would have liked to see how the U-shaped pattern of the directionality index in the case of secondary contact with expansion (Fig3) compares to a simple expansion model?

Following Peter & Slatkin (2013), could the authors perform a statistical test (the null hypothesis being no expansion) to determine the significance of the directionality index between demes? For example, by producing a null distribution based on random permutations of allele frequencies. How does the power of such test (reject isolation-by-distance when there is expansion), and the false-positive rate (inferring expansion when there is isolation-by-distance) depends on different bottleneck intensities and expansion speeds?

In a more practical side, I wonder to which extent the results presented in Fig3 (and in the corresponding supplementary figures) depend on the delimitation of the edges (demes 24–27 and 74–77) and of the centre (demes 49–52 or 50–51). This is obvious for patterns of linkage disequilibrium and genetic diversity for which different signatures are expected if only demes from 50 to 60 are sampled in the field (see FigS1). Could the authors comment on that?
Validity of the findings: The description of the results is clear and the authors did not over-interpret them. Basically, secondary contact can be easily distinguished from migration-drift balance only when the contact is sufficiently recent compared to the total divergence time between the two populations.

I would have moderated the conclusions made lines 248–250, as the directionality index has a distinctive pattern under secondary contact only when the contact is recent (Tc=1, see Fig3). Moreover, this depends entirely on having a series of bottleneck events during range expansion (though, it may be a common feature of population history).
Additional comments: In this manuscript, Bertl and Blum ask whether two spatially explicit models, namely a secondary contact following range expansion, and an isolation-by-distance model with a barrier to dispersal, can be distinguished based on a set of commonly used statistics. The authors address this question by simulations, mirroring the evolutionary history of species which started to diverge during the last Quaternary glaciation in different glacial refuges, and subsequently expanded their range until secondary contact.

Although many recent studies have been conducted to compare different modes of speciation, little has been done to explicitly account for range expansion during the re-colonization process and spatial structure in the suture zone. I particularly appreciate this novelty. The contribution of this paper is also to assess the power of a set of statistics in discriminating between a non-equilibrium secondary contact model and an isolation-by-distance model. I found interesting the use of the directionality index, which leaves a specific pattern in the secondary contact model.

I only have two main negative comments. First, I regret that the authors only considered in the supplemental information a model of secondary contact with a barrier to gene-flow. It is well known that hybrid zones often coincide with geographic barriers to dispersal (Hewitt, 2000), so it would have been worth considering this scenario in the main text. Second, I think it would be useful for readers who are interested in applying the directionality index to their study system to give them a way of testing for the presence of range expansion (as the authors did for the presence of admixture, see Table1).

 References

Barton, N (1979). Gene flow past a cline. Heredity, 43 (3), 333–339.
Bierne N, Welch J, Loire E, Bonhomme F, and David, P (2011). The coupling hypothesis: why genome scans may fail to map local adaptation genes. Molecular Ecology, 20, 2044–2072.
Bierne, N, Gagnaire, P-A, and David, P (2013). The geography of introgression in a patchy environment and the thorn in the side of ecological speciation. Current Zoology, 59(1), 72–86.
Hewitt, G (2000). The genetic legacy of the Quaternary ice ages. Nature, 405 (6789), 907–913.
Nagylaki, T (1976). Clines with variable migration. Genetics, 85, 867–886.
Peter, B, and Slatkin, M (2013). Detecting range expansions from genetic data. Evolution, 67, 3274–3289.


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: CAN SECONDARY CONTACT FOLLOWING RANGE EXPANSION BE DISTINGUISHED FROM BARRIERS TO GENE FLOW?
Review round: 2
Reviewer: 1

Output:
Basic reporting: The structure writing is generally clear, though the English could be improved.  Some points are ambiguous (see below). The references are largely to recent "landscape genetics" plus some older reviews, but there is no engagement at all with the substantial theoretical literature.
Experimental design: The simulations are very limited, and in particular represent small one-dimensional populations.  Patterns will be very different in large 2D populations - which indeed present a considerable computational challenge.

The simulations are only examined using various summary statistics; there is bio examination of the actual patterns driving these statistics, or checks that they match the relevant theory.
Validity of the findings: As explained below, these limited simulation results are likely to be misleading.
Additional comments: The authors say that this is a simulation paper, and are not willing to review the relevant theory.  Sometimes, the theory is intractable, and so one can only simulate. However, in this case there are many straightforward theoretical predictions that give insight into how one might distinguish secondary contact from primary divergence.  One cannot simply ignore it.

One such prediction is that LD is generated by a short-term balance between admixture and recombination. Yet, it is claimed here that LD can be used to distinguish primary from secondary contact.  I suspect that this is just because neutral clines following secondary contact may be much sharper, relative to dispersal.; this will dissipate quickly, except near selected loci, with LD decaying roughly as 1/(rt).  This explanation needs to be checked: is the signal coming from differences in cline width?

A central problem, which is not discussed at all, is that although many hybrid zones may have been formed by postglacial secondary contact, the divergence between hybridising populations has evolved over much longer timescales, and may have arisen in primary contact.  Moreover, the appropriate timescale depends on the spatial scale: near to a barrier, patterns are likely due to recent isolation-by-distance, but fiurther away, reflect much more ancient divergence. This has been quantified  by Nagylaki, and most recently by Barton (2008).

The paper compares various summary statistics under different simulated scenarios, but does not go beyond that, to see what signals are driving the statistics. These statistics rely on either allele frequency differences or LD; one needs to know how the different scenarios affect the underlying genotype frequencies, rather than relying just on some summary statistics.  More fundamentally, the various statistics were devised to test specific models, and should not be used in different contexts.

115 - Scaling to 2N is more usual than to 4N.  Actually, this scaling in problematic in a 1D population, and more important, a small cluster of demes in 1D is completely unrepresentative of a large 2D populatuiion, where coalescent timescales are far longer.

line 137 - If the loci are unlinked, =how can they be on the same chromosome?  Is the model a genetic map length 4 with 100 non-recombining blocks each with 100 SNP? This is not at all clear.

142 - m is more usual to denote mgration rate - mu denotes mutation.

162 - This equation is not appropriate for a 1D cline when there is high migration between adjacent demes, and when there is continued gene flow, not a one-off admixture event.

250 "secondary contact" should not be contrasted with "steppong stome model"!


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: CAN SECONDARY CONTACT FOLLOWING RANGE EXPANSION BE DISTINGUISHED FROM BARRIERS TO GENE FLOW?
Review round: 2
Reviewer: 2

Output:
Basic reporting: 'no comment'
Experimental design: 'no comment'
Validity of the findings: 'no comment'
Additional comments: Bertl and Blum provide an improved version of their manuscript.

They made substantial effort to better evaluate the robustness of their patterns to different sampling schemes (provided in the new section S3); and to assess the power of the admixture test under a range of parameter combinations (provided in new Tables S1-S3). I think these improvements will give useful directions to readers who want to apply the method to their data.

Overall, the methods and figures have been clarified. The authors introduce in more details the different statistics (though, calculation of the admixture coefficient must be made more explicit), and the data & scripts are made available (Figshare repository and Table S4).

I also appreciated that the authors now fully consider the scenario of a secondary contact with a barrier to gene flow in the main document; and they make explicit the difficulty to distinguish it from IBD in the presence of a barrier to gene flow.

Nevertheless, I am not totally satisfied by the answers relative to weaknesses of the theoretical background.
First, although the authors did precise the concepts of secondary contact and barrier to gene flow in the Introduction, I've found the explanations a bit confusing. In particular, the authors must consider rephrasing L44-46 (“not mutually exclusive” sounds peculiar) and L68-70. It is not clear what the authors consider to be “adaptive loci” on L70. An unconditional favourable allele will spread across the species range without being much delayed by a barrier to gene flow (Pialek & Barton 1997). Conversely, a locally adaptive locus will converge to a selection-migration balance.
Second, I agree with the other reviewer that a comparison of the simulation results with the theoretical expectations of IBD and a barrier to gene flow will be a safe check. At least, I would like to see some evidences that simulations are correct in the simplest model.


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: CAN SECONDARY CONTACT FOLLOWING RANGE EXPANSION BE DISTINGUISHED FROM BARRIERS TO GENE FLOW?
Review round: 3
Reviewer: 1

Output:
Basic reporting: 'no comment'
Experimental design: 'no comment'
Validity of the findings: 'no comment'
Additional comments: I am satisfied with this third round of revisions, and I acknowledge the effort made by the authors to provide a theoretical context to their work. In particular, the comparison of the simulation results to expectations of the diffusion theory under secondary contact (Figure S1, S2, S4) and a stepping-stone model (Figure S5) is reassuring, as the authors found an excellent agreement.

I have only one additional comment: at some places, I have the impression that the authors conduct a review of the theory instead of making direct connections with their simulation results. This impression is emphasized by the fact that all new theoretical context is reported in the M&M, while nothing is mentioned in the Results.
For example, the paragraph from lines 156 to 174 basically describes the good fit between simulations and quantitative expectations under the diffusion theory. It would be better included (or part of it) in the Results.
Similarly, the qualitative predictions for “Linkage disequilibrium” (lines 195 to 201), “Genetic variability” (lines 221 to 229) and “Allele frequency correlogram” (lines 242 to 245) may be better discussed in connection with the simulations in the Results.

As a minor point, I was also wondering why the analytical results on LD obtained by Sedghifar et al. (2015) were not use to directly compare the simulated spatial pattern of LD with its expectation? To which extent the model implemented by Sedghifar et al. differs from yours?

Minor comments
- Line 79: typo, “expansion because secondary contac[y] frequently induced by geographical...”

- Figure S8: “migration rate (μ)” should be replaced by “migration rate (m)”.

- Line 155 and 160: it is not clear what are the references for the formula “σ^2=2m” and “σ^2*t”.

- Line 199: this sentence seems a bit out of scope: “They demonstrated that patterns of admixture LD across space and linkage distances can be utilized to robustly infer the timing of secondary contact.”

- Line 241: extra bracket in ”Ringbauer et al. 2018 ))”.


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: SUNSET YELLOW AND ALLURA RED MODULATE BCL2 AND COX2 EXPRESSION LEVELS AND CONFER OXIDATIVE STRESS-MEDIATED RENAL AND HEPATIC TOXICITY IN MALE RATS
Review round: 1
Reviewer: 1

Output:
Basic reporting: In this study by Khayyat, et al., the authors attempt to assess the potential adverse health effects caused by two widely used food additives, sunset yellow and allura red. The authors examined the biochemical, histopathological and ultrastructure changes in liver and kidney of adult male albino rats treated with sunset yellow (2.5mg/kg b.wt), or allura red (7mg/kg b.wt) for 30 days. In addition the authors studied the genotoxic effect of both dyes on white blood cells using neutral comet assay. The main findings of this study were that these food additives increased biochemical markers of hepatic and renal function (ALT, AST, urea, uric acid, and creatinine). This study also revealed a noticeable increase in MDA and a marked decrease in total antioxidant levels in animals treated with these food additives as compared to controls. In addition, both dyes had adversely affected the liver and kidney of the treated animals at the histological and fine structure levels. At the molecular level, treatment with these food additives resulted in downregulation of Bcl2 and upregulation of COX2 expression. Comet assay in white blood cells showed no significant DNA damage in leukocytes.

1.	The current study presents no novelty to the existing knowledge in the field. It is just an ordinary work which will make no real addition to already existing controversy.
Experimental design: 1-The authors did not explicitly mention the gap of knowledge or the scientific void that this study will address.
2-It is not clear why the authors opted to investigate the potential hepatic and renal toxicities of these coloring agents?
Validity of the findings: 1-The results of this work are significantly compromised by the notion that authors used the in vivo comet assay as a sole readout of genotoxicity. Indeed, comet assay alone is not enough to ensure reliable detection of relevant in vivo genotoxicants and should be used in conjunction with the micronucleus test in bone marrow and the AMES assay. Furthermore, it is internationally recommended to use the in vivo mammalian alkaline comet assay rather than the neutral comet assay
2- In the materials and methods sections, the authors indicated that Wistar albino adult male rats were treated with either sunset yellow (2.5mg/kg b.wt) or allura red (7mg/kg b.wt). The authors selected the doses based on a previous study by Doguc et al., (2013). Definitely, the referenced study used the indicated doses of sunset yellow or or allura red in different species of rats (Wistar Han strain) with different gender (female rats) and different physiological condition (Pregnancy)! The authors should mention whether theses doses are relevant to the estimated daily intake (EDI) of these agents.
Additional comments: 1-The authors stated “our experimental procedures are approved with Menoufia University IACUC” committee’s guide for care of laboratory animal (Approval No: MNSP155). However, the study was not performed in Menoufia University and none of the listed authors is affiliated with the institute?
2- It is occasionally noticeable that the authors are trying to inflate their citation counts through self-citation.  This is of particular concern in the materials and methods section, whereas the original articles describing the methods should be cited rather than articles which just used the methods. This improper citation is not a benign practice; adequate and accurate citation is a necessity for scientifically and methodologically sound research.


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

Input:
Title: SUNSET YELLOW AND ALLURA RED MODULATE BCL2 AND COX2 EXPRESSION LEVELS AND CONFER OXIDATIVE STRESS-MEDIATED RENAL AND HEPATIC TOXICITY IN MALE RATS
Review round: 1
Reviewer: 2

Output:
Basic reporting: See combined comments below.
Experimental design: See combined comments below.
Validity of the findings: See combined comments below.
Additional comments: See combined comments below.


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: SUNSET YELLOW AND ALLURA RED MODULATE BCL2 AND COX2 EXPRESSION LEVELS AND CONFER OXIDATIVE STRESS-MEDIATED RENAL AND HEPATIC TOXICITY IN MALE RATS
Review round: 1
Reviewer: 3

Output:
Basic reporting: - The manuscript is written in clear professional English.
- provided with enough background information based on literature review related to the subject.
- The manuscript is in acceptable professional structure.
- It is self-contained with relevant results to the hypothesis.
with no comment related to Basic reporting
Experimental design: - It is stated that "the control group has been previously published in our previous work (Khayyat et el., 2017)"., Line 585;as well as in several other places with table1, 6; and figures.  Does that mean that the control group is part of the present study design or was actually of a previous work and just included with the present results for comparison. If the later, is the case, that is not acceptable for the proper design of the experiment. If it is part of the present design, it is also unacceptable too, since data are published again even if it is of the control data.
- line 98; is not defined where the experiments are carried out?. "our animal facility"-
- line 102; approval of experimental procedure were taken from Menoufia University, while affiliations of authors are in Alexandria and KSA ???.
Comments on these are strongly recommended.
Validity of the findings: - line 155; Student's t-test is not the proper method to use to analyze data statistically. one way ANOVA with a post-hoc test is advisable to compare the 3 groups.
- line 44; 166; 237; uric acid levels were not statistically significant.
- line 353-355; The conclusion should be more defined to include doses used and duration and be limited to the rat species.
- Legends of Table one should include number of rats used and method of statistical analyses.
Comments on these are strongly recommended.
Additional comments: The manuscript needs major revisions related to experimental design and validity of the findings as previously stated beside few editing, such as: line-42; space before mg; line-48; altered; line-91, we investigated the possible effect of both..; line-166, induced a slight non-significant elevation..;


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: SUNSET YELLOW AND ALLURA RED MODULATE BCL2 AND COX2 EXPRESSION LEVELS AND CONFER OXIDATIVE STRESS-MEDIATED RENAL AND HEPATIC TOXICITY IN MALE RATS
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comments
Experimental design: their response to the comments are somehow accepted
Validity of the findings: accepted response
Additional comments: comments are corrected


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: MODELED LARVAL CONNECTIVITY OF A MULTI-SPECIES REEF FISH AND INVERTEBRATE ASSEMBLAGE OFF THE COAST OF MOLOKA‘I, HAWAI‘I
Review round: 1
Reviewer: 1

Output:
Basic reporting: Overall, the manuscript is clearly written and provides novel and relevant results for the field of marine dispersal and connectivity, as well as marine management. The manuscript covers a wide range of information, dealing with various species, several methods and considering important biological and physical factors.

With a clearly written introduction, the authors provide a background that is supported by relevant literature in the field.

The structure of the manuscript follows the expected style of a scientific manuscript and contains subtitles that speak for themselves.

The results obtained provide a background against which hypotheses are tested and which may be used by marine recourse managers as aimed for by the authors.
Experimental design: The manuscript covers a topic that is highly relevant and uses methods (Lagrangian particle tracking and graph-theory) that are increasingly used to estimate connectivity at temporal and spatial scales that cannot be covered using standard observational techniques.

The aim of the manuscript is clearly defined, being the simulation of larval dispersal around Molokaʻi and quantifying island-scale connectivity. Although model simulation should be interpreted with caution and provide output of which the interpretation can be biased strongly by the resolution of ocean data, studies of this kind are relevant for management practices as they provide insight on the importance of processes and patterns that cannot be studied otherwise. Output from this study should ideally be combined with high-resolution genetic data as underscored by the authors.

The methods used are described in detail. Some minor comments are provided in the "comments to the authors".
Validity of the findings: As to my knowledge, a similar study has no been conducted in the study area and has been undertaken clearly with the aim of filling a knowledge gap as to help advising coastal and marine management. As stated by the authors, more biological data is needed and future studies should be improved further by including aspects such as temperature-dependent pelagic larval duration. Despite some well-known limitations of IBMs arising from limited or scattered species-specific data, the authors provide a interesting study that may stimulate as well the collection of data that is needed to increase the realism of this type of models,

The authors did a great effort on compiling the required biological data and using high-quality ocean data. Since the interpretation of connectivity output can be biased by the spatial resolution of ocean data, it is worth to pay some attention to this in the Discussion section. Drawing conclusions from this type of simulations should be done with the model resolution in mind, given that complex coastal processes may be smoothed and hence affect connectivity estimates and simulated trajectories.

Conclusions drawn by the authors are all based by the analysis performed and speculation is limited.
Additional comments: Dear authors,

the manuscript is well-written and provides insight on aspects of dispersal and connectivity that are highly relevant for conservation and management practices. The results are novel and were obtained using techniques that are increasingly used to study connectivity and dispersal at spatial scales at which standard observational techniques cannot be adequately used. Also, the area studies is of high

I hereby provide some constructive and minor comments:
- Throughout the text: sometimes 'Fig. X', sometimes 'Fig X' (see the dot)
- LINE 112: Which bathymetry dataset has been used to run the MITgcm simulation?
- LINE 115: It may be useful to provide the resolution also in km, between brackets for example
- LINE 152: Although the condition to define settlement is arbitrary and not always straightforward, I wonder about the background against which the 3-km contour has been chosen?
- LINE 178: Caranx should be italicized;
- LINE 194: It would be valuable to know which aspects of the “surrounding geography” were considered in the pooling phase.
- LINE 290 and Fig. 6: It is interesting to note that the “dip” in all three kernels is close to 30-35 km. I wonder how this could be explained, what the underlying process may be. I apologize if I have missed this in the text.
- LINE 323: replace ‘shows’ by ‘showing’
- LINE 525: there is  double comma - [...] & Cowen, 2007),,
- Caption Fig. 1: It may be useful to provide the absolute (rather than a relative) resolution ("longitudinal resolution of 1:50 [...]") as to avoid that readers have to go back and forth to keep track of numbers.
- Caption Fig. 3: species names should be italic
- Figure 9 and Figure 11: species names on x-axis should be italicized


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: MODELED LARVAL CONNECTIVITY OF A MULTI-SPECIES REEF FISH AND INVERTEBRATE ASSEMBLAGE OFF THE COAST OF MOLOKA‘I, HAWAI‘I
Review round: 1
Reviewer: 2

Output:
Basic reporting: The language is clear and professional throughout. The manuscript is well-referenced. For the most part it follows PeerJ standards; However, there’s a fair amount of discussion in the Results section, and the Discussion section is broken further into Discussion and Conclusion sections. The authors may want to tidy this in accordance with PeerJ standards. I’m unsure if PeerJ allows a “Results/Discussion” section.

There are a few instances where the convention used to identify species changes – the authors should review all use of genus and species, to be sure they are correct.

Figures are of general high quality. I have a few suggestions for specific figures, which I will give in the General Comments.

The raw data is supplied. However, it is given in a single large “connectivity” file, without sufficient metadata or explanation of column headings. This file may not be adequately accessible, and the authors might consider breaking it apart by species. Also, larval trajectory data is not provided, which would be required to assess how the physical environment or depth of a virtual larva may affect study results or connectivity.
Experimental design: This study meets the experimental design standards of PeerJ. There are some clarifications that could be made in the methods, and these are outlined in the General Comments.
Validity of the findings: For the most part the findings of this study appear valid and are adequately discussed. There are a few instances where interpretations of a result should be tempered, especially when discussing recruitment or archipelago-scale connectivity. These are discussed in the General Comments.
Additional comments: a.	Major concerns:
i.	Local retention vs. Self-recruitment. The authors claim to have estimated levels of self-recruitment using their model, but this is not the case so far as I understand. In order to estimate self-recruitment, total recruitment must be known, and without inputs from adjacent islands, it is not clear that total recruitment is known. Thus, the authors should be estimating local retention, which is the proportion of larvae produced locally that recruit locally. This may be a better indicator of local persistence than self-recruitment, anyway.
	Importantly, this issue highlights a larger issue in the manuscript, where the authors do not adequately couch their results/discussion with the acknowledgement that their dispersal experiments/results exist in a larger system of larval dispersal and exchange. This issue may come up multiple times in this review. As another example, on line 366 a paragraph describing larval export uses vague language that could easily be misconstrued to exaggerate the “importance” of Moloka’i larval export to other islands in the archipelago. Because archipelago-wide dispersal was not modeled, statements like, “… 83%... of larvae settling to O’ahu were spawned on the north shore of Moloka’i…” are misleading without clarification that this is a percentage of the total larvae migrating from Moloka’i to O’ahu (not of O’ahu recruitment), which is itself some proportion of total larval exchanges modeled. There are other examples of where the language needs to be refined throughout the text.

ii. 	Scales of dispersal. The authors acknowledge that the diverse species traits modeled result in species-specifically shaped networks, but I’m not sure the choice or handling of metrics is adequate. For example, when comparing networks, edge density likely requires that the number of possible connections to be equal between the networks. In this study this is not the case, so far as I am aware. Thus, if there are fewer possible connections (fewer habitats in the network), edge density is more likely to be high than in a larger network with more habitats (even if the actual number of connections between habitats of interest is the same between both networks). Thus, as it stands, this is not a great metric – even though the conclusions drawn from the analysis may indeed be sound.
	Further, the BC analysis needs to be addressed. We know that different species in the model have a different number of connections to other reefs in the archipelago (and even within Moloka’i different species have different habitat nodes). When making comparisons, BC is only useful if the nodes of the networks are the same. Thus, on line 423, where BC comparisons are discussed, the authors need to be sure that the networks are indeed comparable in this way. In addition, BC will change substantially as habitats are added to the network. Are the exogenous sinks included in the BC analysis? Discussion of BC in this case needs to acknowledge that only local connections are being assessed.

iii. These models are probabilistic, but the probabilities associated with connections aren't really addressed.

b.	Other considerations – in the order that they appear in the manuscript:

L135-141: Interesting that land and benthic masks were not extracted from the MITgcm. Not a criticism, but I’m curious how these coastal and benthic masks overlap with the hydrodynamic mask.
L145: Were w velocities in the model? If not, did particles move up and down in the water column, or were they statically associated with a specific depth?
L153: This is also very interesting, and different from many other particle tracking models. I’m concerned with how this random distribution of PLDs interacts with mortality. I understand that mortality was modeled using a half-life, but it seems PLD is randomly distributed. If a particle’s individual PLD is reached before it finds habitat, and before its ‘mortality’, does it die? Does this imply that mortality is higher than stated in the methods?
L158: There doesn’t appear to be a table summarizing the releases for each species. This could be incorporated into Table 1.
L171 and throughout: Review to make sure that Latin names are being handled appropriately. Also, and for example, I believe the use of Cellana spp. sometimes drops the “spp.”.
L245: I believe this information needs to come earlier.
L261: Italicize o and s.
L265: Should it be rearward proportion rather than probability?
L273: I think “longer time to competency” is more appropriate here than “higher PLDs”?
L303: Are recruitment sites on other islands included in this edge-density estimation?
L314: A loud and clear distinction needs to be made that “connectivity” is referring to within island connectivity, right?
L338: I agree with the authors here, and think this statement needs to be made even more obvious, and the concept referred to throughout.
L358-363: The authors make this seem like a small percentage (5% or 7%), but doesn’t this seem like a very large percentage? 7% of total recruitment in the model was interisland exchange with Maui… that seems significant to me! Part of the difficulty is that these aren’t translated into probabilities.
L366: Please address language in this paragraph that is a bit misleading (discussed above).
L383: … (Figure 8)…?
L385-396: This whole paragraph needs to be re-worded to address some sort of “regional” retention, in my opinion. It’s also unclear if these “realized” connections have high probability. This larval dispersal model should be probabilistic, but probabilities are not really addressed in this analysis. Is a very low probability connection “realized”?
- General question - : What happens to deep dispersers if they encounter shallower water?
L403: Vague sentence. Between the north and south coasts? Within them?
L412: “Bigger picture…” also vague.
L473: I think it would be great to highlight the Park on the maps, maybe showing the park boundaries. Another figure to consider is showing spillover connections from the Park.
L504: Again, I think it needs to be made clear that connectivity is within a small domain. Longer PLDs would likely be correlated with higher connectivity in a larger domain.
L525: ,,
L556: This section may not be necessary here. It could be moved to Intro/Background.
L620: I don’t think this claim can be made, at least in this fashion. There’s no evidence it’s an “important” source, although you have shown it is a potential source. There’s no indication what proportion of total recruitment the connectivity you’ve demonstrated would represent, nor what the probability of arrival might be.
Table 1: The “Spawn period” column could be made clearer. Maybe: (D-D/HR-HR). The ordering of superscripts is hard to follow. Could add the total number of releases.
Fig. 1: Possible to indicate or color the island of Moloka’i?
Fig. 4: It’s not a HUGE deal, but it’s a little vague how these regions were chosen and groups made.
Fig. 5: (Note my earlier concerns about edge-density, also retention). Might be helpful to include PLD, time to competency, # particles released, etc. in this figure, maybe up above the results.
Fig. 8: Y-axis – proportion of what?
Fig. 10: (Note concerns about calculating BC). Consider making the arc-direction consistent, so that connectivity is, for example, always clockwise along an arc.
Fig. 11: There’s a duplicate panel (two BC).
Fig. 12: These could be indicated in Fig. 10.
Fig. 13: Consider using Latin names here. The inconsistency makes it difficult to interpret. Also, I suggest labeling the settlement locations as “Moloka’i” and “Other island”, or similar.


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: MODELED LARVAL CONNECTIVITY OF A MULTI-SPECIES REEF FISH AND INVERTEBRATE ASSEMBLAGE OFF THE COAST OF MOLOKA‘I, HAWAI‘I
Review round: 1
Reviewer: 3

Output:
Basic reporting: -	The English language is clear and professional throughout the manuscript. The use of some abbreviations is sometimes excessive (particularly in the figures captions). The past tense is required in Introduction, Methods, and Discussion. The beginning of each section should be indented.

-	The structure of the manuscript is conformed to Peerj standards. Some sentences in the Results should be moved to the Discussion (see General comments).

-	The introduction and background are showing the context and the literature is relevant. The structure of the introduction needs to be clarified and some information added. Change to past tense.

-	The figures are high quality. However, the number of figures is high and some of them are not relevant for the comprehension of the study. For example, Figures 3 and 4 should be combined and Figure 12 moved to the Supporting Information. Some of the captions need to be modified and legend is often missing (see General comments).

-	The results section is very large and some of the results are not relevant for the main questions of the study (see General comments).

-	The raw data are supplied.
Experimental design: -	The research is original and within the scope of Peerj.
-	The study was performed rigorously.
-	The methods are well described and enough details are given to replicate.
Validity of the findings: The results are meaningful and the data is robust. The authors performed a lot of analyses. However, more focus should be done on the relevant results (see General comments).
Additional comments: Title: precise that your manuscript is about larval connectivity.

Introduction
Lines 40-55: This first paragraph contains good background information but should be reorganized. First describe why studying larval dispersal/connectivity is important for management; next describe the larval dispersal phases.
Lines 59-61: Genetic and microchemistry studies applied to larval dispersal should be mentioned here (see Leis et al 2011).
Line 71: what do you mean by “larval physiological characteristics”?
Lines 70-73: You should also discuss about pre-competency period and fecundity. This sentence should be re-written.
Line 74: Remove “in the form of”
Line 75: The name of the hydrodynamic model without describing it in the introduction is not understandable. Just mention “hydrodynamic” or “oceanographic” model.
Line 75: “…fine-scale patterns of larval exchange…”
Line 103: The use of “Here” is not really nice in a publication. Instead, use “In this study…”
Line 104: “… to quantify the larval exchanges…”
Lines 103-110: You need to better describe the main research questions of your study (i.e., effects of biological factors on larval connectivity, larval supply from Moloka’i, regional connectivity patterns)

Methods
Use past tense in Methods.
Line 113: Your paragraph should start with: “The hydrodynamic model used was…”
Lines 127-129: The potential effects of El Niño or La Niña events on larval connectivity should be more described in the discussion.
Lines 129-131: What did the comparison show?
Line 149: What do you mean by development?
Line 153: Explain why you chose to randomly assign a PLD value instead of taking a mean PLD for example. Did you run simulation with fixed PLD? Have the results changed?
Line 158: “… equating from…”
Line 158: Those numbers should be added in Table 1 for each species.
Lines 159-163: What about larva pre-competency period? Mention if no data was available.
Line 179: and instead of with
Line 179: August-December
Lines 193-194: The regional description of the habitat needs to be clarified. What are the groups 2 to 11 mean? (2 to 11 instead of 2-11).
Lines 244-257: not sure why you are talking about self-recruitment to evaluate source-sink dynamics. Another metric that is important to consider, particularly for self-persistence, is local retention. Why studying self-recruitment?

Results
Authors should re-write the Results section. This section is too long and we lose the flow of the important findings. The authors need to keep the more relevant results for their study. Also, some sentences belong to the Discussion.
Lines 267-343: please reference to the names of each metric from Figure 5. Sometimes, we do not know which metric you are talking about.
Line 282: …4% for?
Lines 300-313: I believe you should refer to Figure 5 here again (same in last paragraph)
Line 344: With a larval dispersal model, you do not have results on recruitment. You need to change recruitment for settlement throughout the manuscript.
Line 347: Is figure 7 about self-recruitment? It looks like you only have settlement information on Figure 5. Please precise and modify if necessary.
Lines 350-356: This statement is for the discussion.
Lines 363-365: Results are discussed in the Discussion. Move this to the Discussion.
Lines 366-374: Which figure shows these results?
Lines 378-383: These statements are for the discussion.
Lines 385-396: Figure 9 is showing density values and you are describing percentages.
Lines 393-396: Discussion.
Lines 397-409: Where do these percentages come from?
Line 411: “(as defined in Figure 4)”
Lines 432-472: You give too much detailed information. You need to focus on the relevant results for your study.

Discussion
Use past tense.
Line 494: “In this study…” instead of Here
Line 499: “depth of larval distribution” instead of larval dispersal depth
Lines 518-526: and pre-competency period?
Lines 536-539: The same sentences are in the Methods. Remove them from here.
Lines 543-546: How the connectivity patterns could be affected? Give examples with references.
Line 555: You should also have a paragraph about the effect of the abiotic factors on your results. Some of that is mentioned in the Results section and can be moved here.
Line 556-566: I don’t understand the pertinence of this section. Graph theory has been applied to larval connectivity in several previous studies. Why don’t you write about the relevant results that are obtained with graph theory here?
Lines 572-577: This should be in the paragraph about effects of biological factors.
Line 584: settlement instead of recruitment
Lines 586-598: This is not related to the topic of this section. Should be moved.
Line 643: Why are you talking about local retention here?
Lines 644-647: These are important results and are unfortunately lost in the large flow of all the results you are presenting. You need to focus on these results throughout your manuscript.

Table
Table 1: DoY? Day of the Year
Figure 1: You are starting the caption by “Displaced…”. You need to make a sentence. Add “and” after “December 31st, 2011,…”. A color legend referring to the velocities values is better than describing that in the caption. You do not really describe this figure in your manuscript. You can put it in the appendix.
Figure 3: Spawning sites.
Figures 3 and 4 could easily be combined. Also in Figure 4, does each color represent a specific habitat? Precise.
Figure 5: L-R?
Also write “divided by” instead of putting /.
“Mean and maximum...”
“Proportion” and “maximum” in the Figure.
Figure 6: It is hard to distinguish between the colors. Do not fill the areas under the curve and put a different color or type of line for each curve.
Figure 9: Specify that the results in this figure are for Moloka’i.
Figure 10: Add in the figure which ones are short/medium/long dispersers. Also avoid abbreviations in caption.
Figure 11: Having a color legend with values is better than describing it in the caption.
Figure 12: This figure does not give a lot of information. It should be in the appendix.