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: KNOWLEDGE AND BELIEFS REGARDING CERVICAL CANCER SCREENING AND HPV VACCINATION AMONG URBAN AND RURAL WOMEN IN LEÓN, NICARAGUA
Review round: 2
Reviewer: 1

Output:
Basic reporting: 1.	I thank the authors for re-framing their manuscript from barriers to beliefs regarding cervical cancer screening so that their focus is more aligned with what was actually measured. However, the rationale for measuring beliefs is under-developed. One way the authors could strengthen their rationale is by discussing how women's beliefs regarding cervical cancer screening and HPV vaccination might influence (i.e., promote or inhibit) their uptake of these HPV and cervical cancer prevention strategies. This would make most sense prior to line 30 in the Abstract and line 103 in the Introduction.

2.	It is unclear what the authors mean by “beliefs to promote or limit” in the Abstract (lines 34-45) and Introduction (line 107). If the rationale is further developed as suggested above, the authors could replace “to promote or limit” with “regarding.”

3.	Line 40: Since the outcome was women’s belief scores, "and attitudes" should be deleted from line 40.

4.	Line 41-42:  This sentence should be deleted (“The outcome variable was the screening-promoting belief score.”).  It would make more sense to define the outcome before (i.e., in line 39) describing the analysis.  For example, “We assessed women’s beliefs regarding cervical cancer screening via a 22-item scale, with higher scores indicating screening-promoting beliefs.”

5.	The authors’ suggested revision to lines 42-43 should be incorporated into the abstract: Twenty qualitative interviews, which sought to explain sociocultural dimensions of 	knowledge and attitudes indicated by our quantitative findings, were conducted with a sample of 13 urban and 7 rural women (aged 19-46).

6.	I think the manuscript is greatly improved by shifting the focus of the manuscript to beliefs regarding cervical cancer screening. However, I think the manuscript requires a careful review to ensure that all aspects of the manuscript are up-to-date with respect to this shift in focus. For example, themes (1) and (2) sounds more like barriers than “knowledge and beliefs” regarding cervical cancer screening. Theme (5) also seems out of place with this description. Please revise (Abstract lines 46-55, each theme in the Results section, and lines 454-463 in the Conclusions section) to more clearly convey how these themes represent knowledge and beliefs.  Perhaps attitudes towards cervical cancer screening would be an appropriate addition to the description of the themes identified?

7.	Lines 55-56: Because this result is from the multiple linear regression analysis, this sentence should be presented with the quantitative findings above (i.e., before the presentation of qualitative findings).

8.	Line 126: What is "reported acceptance"?  The authors should consider deleting the word "reported" here.

9.	Line 177-178: The latter half of this sentence describes how the belief score was analyzed (i.e., with respect to demographic characteristics and participant knowledge) and should be deleted as that information belongs in the Quantitative Data Analysis section.

10.	Lines 183-187: While some items listed in Appendix B reflect positive statements (i.e., Pap tests are safe), most of the items listed in Appendix B reflect negative statements. Thus, it’s unclear how assigning a score of 1 if participants agreed with a negative statement would yield an overall score where higher values indicate screening-promoting beliefs. Please verify that the scoring is reported accurately and clarify if necessary.

11.	Line 228: Knowledge should be deleted here since the women’s belief scores were used as the outcome, while knowledge of HPV and cervical cancer were explanatory variables of interest.

12.	Lines 403-406: It’s great to see that these data have been added to the manuscript; however, these data would be more appropriately reported with the quantitative data at the beginning of the Results section.
Experimental design: The authors acknowledge that their sample is biased due to the fact that women were recruited from health centers, but their data suggesting that the majority of women in their sample are in compliance with national guidelines (lines 403-406: “80% of women at the health centers had received a Pap smear within the past year, with 37% of women screened within the past 3 months [Table 4]”) are in stark contrast to the estimate provided in the Abstract (line 30) and Introduction (lines 86-87): “only 10% of women receive Pap smears at the nationally recommended frequency.”  This large discrepancy should be addressed in the manuscript.
Validity of the findings: Some of the authors qualitative findings directly highlight the mismatch between beliefs and actions (e.g., the quote from Participant 16 on lines 301-306). Because this study measured beliefs regarding cervical cancer screening rather than actual barriers to screening, it would be helpful if the authors further developed their discussion of how their findings could be used to develop interventions to promote cervical cancer screening and HPV vaccination.
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: KNOWLEDGE AND BELIEFS REGARDING CERVICAL CANCER SCREENING AND HPV VACCINATION AMONG URBAN AND RURAL WOMEN IN LEÓN, NICARAGUA
Review round: 2
Reviewer: 2

Output:
Basic reporting: This is a revised paper sharing results from a study in Nicaragua to understand knowledge, attitudes, beliefs about cervical cancer screening and HPV vaccination. This manuscript has improved since my prior reading, however there are still some issues that should be addressed prior to acceptance.

The language is clear. I suggest adding to your methods that the interviews and data collection occurred in Spanish and was translated after (or before) data analysis. I also suggest adding URLs to your references to allow readers to access your referenced documents. Lastly, the conclusion needs some editing to be more specific to the results from this particular study rather than sweeping statements- I have given some examples below.
Experimental design: The research question for phase 2 (qualitative) is not clearly articulated and different language is used to explain the purpose of this phase in different parts of the manuscript. Please see below.
Validity of the findings: Please see comments regarding the conclusion below.
Additional comments: -Abstract: It is redundant to say your simple linear regression analyses were unadjusted and multiple linear regression was adjusted.

Introduction:
-Line 70: Please provide a reference for “The vast majority of cases of cervical cancer are caused by persistent infection with specific strains of human papilloma virus (HPV).”

-Line 72: Please provide a reference for “In addition, screening through the use of cervical cytology is an extremely effective method to identify pre-cancerous lesions and prevent the development of cancer.”

Methods:
-Line 127-130: “The preliminary quantitative results influenced the creation of the open-ended discussion guide, which sought to elucidate sociocultural dimensions of knowledge and attitudes about HPV, cervical cancer, screening practices, and acceptance of HPV immunization that might further explain our quantitative findings. “ Is this sociocultural dimensions of knowledge, attitudes and acceptance, or personal/individual level dimensions? Later in Line 141-142 you state “The interviews thus placed a greater focus on understanding attitudes and beliefs towards HPV and cervical cancer.” This seems different than the aims previously stated. Then again later in Line 234-236 you state: “The purpose of Phase Two was to expound upon quantitative findings regarding gaps in knowledge and past experiences with Pap smears, HPV and cervical cancer. In addition, the interviews enabled a conversation regarding the views of women on a potential HPV vaccination program in Nicaragua.” These should be consistent and there is no reason for repetition. I suggest providing the aim/purpose clearly and concisely for phase 2 one time.

-Line 207-211: What was the reference level for your dummy variables?

Results:
-Line 274-276: “Fewer than half of the participants completed secondary school (46%) in both the urban (48%) and rural (44%) populations.” Looking at your table, that category is not completion of secondary school, but any secondary school. In addition, this doesn’t look like the accurate percentages – you can add categories together to stratify in this way.

-Table 3: Define “belief score” in a footnote.

-You present some data on health insurance. Please introduce the reader to the health insurance system in Nicaragua. Is any healthcare provided by the government? Are preventive health services like Pap Testing provided at a charge?

Conclusions:
-Thank you for the addition of Table 4. Table 4 demonstrates that almost all participants had had a Pap test within the past 3 years - just as the guidelines recommend. Therefore this sentence from line 455 (and other sentences from the conclusion) may not be relevant: “Our results suggest that women may be dissuaded from seeking regular screening due to embarrassment associated with the intimate nature of the exam as well as the association of Pap smears and cervical cancer with sexual promiscuity.” These contrasting results should be discussed. In addition did women specifically say that they were “dissuaded” from seeking regular screening? Or did they say that this was an issue they faced?

-Line 458: Did you measure health center attendance?

-Note: HPV vaccine is important for both males and females and may prevent cancer in both men and women. I suggest mentioning this in your discussion and providing an explanation as to why you focused on daughters rather than adolescents in general.


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: DIVERSITY OF FISH SOUND TYPES IN THE PEARL RIVER ESTUARY, CHINA
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: General suggestions:
1.In Result section, the authors mentioned 23 sciaenid species had been recorded in Hong Kong waters by citing a 1999 paper. Information about the sciaenid species occurring in the survey area in more recent years, if available, is useful to help confirm the caller’s identity. The voluntary calls of J. macrorhynchus and J. belangerii match some of the call types, it is expected that these two species should present in the study site.
2.The authors should give the relative abundance of each call type occurring in each recording day (or in each of the two continuous recording session) if possible. This information is helpful to interpret number of soniferous species in the area that produced these 66 call types.
3.Please aware that no vertical lines should be used in tables.
4.All characteristics of 3-8 section calls are presented in the supplementary section. It is suggested to add one figure following Fig. 7 to illustrate three of these call types.
5.Comparisons were made among the call types recognized in this study with the hand-held disturbance sounds of several sciaenid species published in the literature and no match was noticed except for Johnius macrorhynchus. Despite of the similarity among the disturbance and voluntary call types in J. macrorhynchus (Lin et al., 2007), this condition may not be a general rule for other sciaenid species. Hand-held disturbance call might be a vocal response toward the highest stress to a fish and this high stressful condition may not be the one causing the voluntary calls heard in the survey site. The purrs emitted when the fish was confined in a small tank, the repeating cycle reduced (with a longer pulse period).
Johnius macrorhynchus emits two call types (Lin et al., 2007), the dual knocks and the purr. It is possible that J. macrorhynchus emit these two types in series and creates a multiple section call type.
6.The spotted seatrout (Cynoscion nebulosus) is one of the few sciaenid species that produces as many as four types of call (Mok, H.k. and R.G. Gilmore. 1983. Analysis of sound production in estuarine aggregations of Pogonias cromis, Bairdiella chrysoura, and Cynoscion nebulosus (Sciaenidae). Bulletin of the Institute of Zoology, Academia Sinica. 22(2): 157-186.). It is likely that most sciaenid species have fewer call types. Because there are 66 call types recognized in the survey sites, one can guess some of the call types must come from a single species.
As most of the call types were identified based on the number of sections and the repetition of the anterior section, it is likely that a species might be able to produce several call types by varying the anterior sections of the call as a response to the variable external stimuli.
According to the result of cluster analysis, five clades were revealed. Can the authors hypothesize that these groups belong to the call repertoire of five species?
7.Spiny croaker is a small croaker species, its call type could be distinct to other related species due to it small sonic muscles.
8.Huang (Huang Po-Wei. 2016. Sound characteristics and spatiotemporal variability of Scienidae in the coastal water of northwestern Taiwan. Master Thesis, National Dong Hwa University, 109pp.) recognized only four call types from three recording sites on the northwestern coast of Taiwan where 9 sciaenid species have been recorded (Johnius amblycephalus, J. distinctus, Lamichthys crocea, Nibea althiflora, Pennahia anea, P. argentata, P. microcephalus, P. pawak, and a undescribed Johnius sp. which has been has been misidentified as J. macrorhynchus. The call type is identical to the purr call of ‘J. macrorhynchus’ was the most abundance type at these sites. The soundscape was dominated by only one sound type.
9.Please explain how the order of the call types in Fig. 8 was decided?

Specific suggestions:
1.Line 22, ‘species-specific sound’ should be use cautiously because sounds of some soniferous fishes might to so similar that they don’t have a species-specific call type.
2.Line 70, : ‘sp.’ should be changed into ‘sp.’ (in italics)
3.Line 71: : ‘spp.’ should be changed into ‘spp.’(in italics)
4.Line 88: ‘Nibea diacanthus’ should be changed to ‘Protonibea diacanthus’.
5.Line 101:’ the spatial and temporal patterns of soniferous fishes, should consider to be changed into ‘the spatial and temporal distribution patterns of soniferous fishes in the estuary’.
6.Line 102: ‘of the damage to aquatic environments’ may consider to be changed into ‘of the damage to aquatic environments (e.g., spawning grounds of the sciaenids)’.
7.Lines 202-205”… and the call duration was dependent on the number of pulses in a call these parameters were not included in the PCA, Canonical discriminant analysis and hierarchical cluster analyses.” However, pulse number in a call was a parameter valuable in matching call type 1+N19 with the known voluntary call of Belanger’s croaker. As such call duration remains a useful taxonomic character.
8.In line 261-262, ‘Hierarchical clustering using a between group method that measure the squared Euclidean distance automatically group the 31 extracted call types…’. Please distinguish ‘the 31 extracted call types’ with the 66 call types mentioned elsewhere in the text.
9.Line 352: ’underhand held condition’ should be changed into ‘under hand-held condition’.
10.Line 501: ‘chinese ‘ should be changed into ‘Chinese’.
11.Line 504 : ‘spp.’ should be changed into ‘spp.’ (in italics)
12.Line 364: ‘sp.’ should be changed into ‘sp.’. *(in italics)
13.Line 12: ‘Soundfrom’ should be changed into ‘Sound from’.
14.Line 362: ‘Sound from other soniferous families, including cutlassfish (Trichiurus haumela, family Trichiuridae)(Ren et al., 2007)’. Because the subject of Ren et al. (2007) paper is about the sound of large yellow croaker (not about the cutlassfish sound), I suggest the authors should recheck if cutlassfish is actually soniferous.
15.Species names in the references should be printed in italics.
16. Lines 681, 692, 701, 702, 704, a full stop should be put behind the table number.


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: DIVERSITY OF FISH SOUND TYPES IN THE PEARL RIVER ESTUARY, CHINA
Review round: 1
Reviewer: 2

Output:
Basic reporting: see below
Experimental design: see below
Validity of the findings: see below
Additional comments: The sheer number of figures (often multiple panel) and tables as well as non standard nomenclature to describe the sounds, prevents me from investing the time to adequately review this manuscript.

I suggest the authors give serious thought about what and is not necessary as most of the figures are unneeded even as supplemental files and revise the manuscript to length that is more fitting its overall content


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: DIVERSITY OF FISH SOUND TYPES IN THE PEARL RIVER ESTUARY, CHINA
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: 1. Line 49: I suggest that the authors should consider changing the word ‘Most’ into ‘Some’.

2. Line 60, ‘Pseudoscianea crocea’ should be changed to ‘Larimichthys crocea’.

3. Line 71: ‘(signature)’ is suggested to be deleted.

4. Line 87: ‘water proof’ changed to ‘waterproof’.

5. Line 115: ‘Total call duration’ changed to ‘Call duration’.

6. Line 150: ‘Fig. 4-5’ should be changed to ‘Figs. 4-6’.

7. It is suggested that (1) at least one representative call type of each call category differing in number of sections should be included in figures 4-6 so that they can be cited in the text (i.e., putting at least one representative call type for 1-8 section calls in these three figures); (2) some redundancy or highly resembling call types original placed in these three figures should be reduced; (3) figures and tables in the supplementary section should not be cited in the text. If these suggestions are accepted, then (Fig. S1-S26) in line 150 should be deleted.

8. Line 178: ‘Ethical statement’, I don’t think this study involves ethical issue with the animals surveyed as only the biological sounds in the field were recorded by an noninvasive method.

9. Line 230-231: “Call types with an analyzed number greater than five were extracted for further discriminant and cluster analyses and 31 call types meet the requirement.” Does it mean that these 31 types were more common than the other 35 call types in this study site? If this is true, then it should be stated clearly in the Occurrence pattern of call types in Discussion (line 353 or other more appropriately part of the text) to give an idea about the relative abundance of the 66 types. Also see comment 17.

10. Line 268: ‘with Sciaenidae sounds’ should be changed to ‘with sciaenid sounds’

11. Line 327: ‘of the species’ should be changed to ‘of the sciaenid species’ and Line 329: ‘Sciaenidae’ should be deleted.

12. Line 335: ‘Arius sp.’ should be changed into ‘ Arius sp.’ (‘sp.’ following a generic name should not be in italic type.)

13. Line 341: ‘Comparison with other passive acoustic monitoring sounds’ is suggested to be changed to ‘Comparison with biological sounds from other passive acoustic monitoring sites’

14. Line 360: ‘come from a single species’ changed to ‘come from the same species’.

15. The problem with peak frequency was discussed between Line 375-378, as length of the sonic muscle fibers with also related to body size, this factor should be mentioned as well.
   The book chapter by Parmentier, E and M.L. Fine., entitled, ‘Fish sound production: insights.’ (In R.A. Suthers et al (eds.). 2016. Vertebrate Sound Production and Acoustic Communication, Springer Handbook of Auditory Research 53, Springer International Publishing Switzerland, DOI 10.1007/978-3-319-27721-9_2) should be cited.

16. Line 637: “inter-pulsepeak interval’ differs from ‘inter pulse peak interval’ used in labelling the X-axis of Fig.4 B. Please check.

17. There are too many insets within Figures 4-6. For example (1) Characteristics of the (A) N9, (B) N10, (C) N13, (D) N17 call types were given. The authors should consider leaving just N9 and N17 in this figure. (2) The insets on regression of call duration and number of pulses in a call for each call types are not necessary.

18. In Table 1, ‘Typ and e’ in the upper left corner of the table are separated ; they should be together.


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: STATINS: ANTIMICROBIAL RESISTANCE BREAKERS OR MAKERS?
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: I consider that the review is well-written and well-structured. It provides new information related to the antibacterial effects of statins, which results useful for the control of bacterial infections that can become in resistant strains. The review gives information about the evidences that deal with the development of bacterial resistance in response to statins, and those that agree with the opposite effect (“AMR breakers”) of these molecules.

In my opinion, this review is worth to be published in PeerJ.  I only have minor concerns that should be corrected in the manuscript:

1.	In line 284, authors describe that the mechanism for the antibacterial effects of statins could be apoptosis. Please, eliminate this sentence, since apoptosis is a cell death mechanism restricted to eukaryotic cells. The term “apoptosis” to explain regulated cell death in bacteria is under discussion, and its molecular basis are very different from that detected in eukaryotic cells. For your reference, Microbes Infect. 2013 Jul-Aug;15(8-9):640-4. doi: 10.1016/j.micinf.2013.05.005.

2.	The period (.) before each reference is wrong. It should be located after.

3.	The sentence in Lines 285-288 is confusing, and it appears contradictory: How the reduction in a metabolite in the mevalonate pathway, essential for bacterial membrane stability, can protect bacteria from statins’ cytotoxic effects? It should be the opposite effect. Please, clarify.

4.	Is there any study related to the analysis of microbiota in people under prolonged statin treatment? This kind of information is missing in the review, and will strength the discussion related to the negative effects of statin against microbiota.


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: STATINS: ANTIMICROBIAL RESISTANCE BREAKERS OR MAKERS?
Review round: 1
Reviewer: 2

Output:
Basic reporting: This work presents a compilation of MIC data for Statins against Gram-positive and Gram-negative bacteria (Results and Tables 1 and 2), proposed mechanism(s) of action of Statins, and knowledge gaps in the field.

The manuscript is well written. References, background and tables are provided in sufficient detail.

Line 235 – Title needs editing. (suggestion: Fungal origin does not correlate with antibacterial activity/efficacy.)
Experimental design: Although a summary of the current status of research on Statins may be useful for researchers in the field, the specific aims and scope of this review are unclear.

In the Introduction (Conclusion), it is claimed that this review 'provides evidence' of a link between statins and antimicrobial resistance. This is inaccurate, as the only data presented in this work are MIC values from previous studies and molecular structures of Statins. At best, this manuscript proposes how synergistic use of statins with other antibiotics may affect microbial outcomes.

As detailed in section 3 below (validity of the findings), the utility of summarizing the MICs is not obvious, especially in the light of significant variation in MIC data and the limited scope of MIC assays as tools for understanding mechanism of antibacterial action.

It is suggested that whether statins support or oppose primary drugs in their killing action is contextual. Several examples are presented in the discussion section, based on previously published works. Although this is a significantly important part of the review, it seems disconnected from the previous analysis of MICs and plausible mechanism.
Validity of the findings: The Results section summarizes MIC values of various statins reported in the previously published studies. The authors then go on to list the potential pitfalls of MIC analysis, including differences in assay times, growth media and other experimental conditions (e.g. with or without shaking). Given the large variation (~5-fold) in MIC values reported for the same statin with the same bacterium, the utility of the MIC comparisons made by the authors seems limited. It is important to note that MIC assays have a limited scope as far as elucidating the mechanism of antimicrobial action is concerned. Within these limitations, the authors have analyzed the structures of Statins and proposed a plausible mechanism of action, namely binding to the bacterial outer membrane proteins, wall teichoic acids and lipoteichoic acids. It is not clear how the authors arrived at this based on their analysis of MICs and/or the structure of Statin molecules.

I urge the authors to clarify how the quarternary chiral carbon, and attached methyl groups, might affect the mechanism of action? Suggestion of a possible interaction between the methyl groups and alanine groups of teichoic acids is speculative. Is there data on Statin-bacteria interactions to support this statement? For e.g. are there any docking studies of the di-methyl moiety to components of LPS, lipid bilayer, outer membrane proteins, etc?

Lines 55-59: Difference in the MIC and sub-MIC regimes is not clear. Both seem to involve growth of resistant bacteria and inhibition of growth of susceptible bacteria.

Lines 103 -106 are identical to lines 15-18.

Line 113 – ‘relative’ and ‘comparison’ are redundant. ‘quantitative’ comparison might be more appropriate. If the authors agree, this change should be made for all instances in the text.

Line 251 – Absence of antimicrobial activity of PRV could be due to other factors (for e.g. absence of quarternary chiral carbon, which the authors have suggested might be important for binding to outer membrane components). These may be essential or preceding steps in the action of statins, prior to involvement of the dihydroxy acid moiety. Therefore, inhibition of HMG-CoA could still be one of the mechanisms of action of statins.

Line 321 – Binding to statins to proteins is suggested as one of the mechanisms of the inhibitory action of Statins. The readers might benefit from a table summarizing the % binding for various Statins.

Lines 326-336: The hypothesis that more membrane area per volume requires more statin molecules seems an oversimplification. There could be other differences between MRSA and MSSA that may explain the difference in MIC values. For e.g. It is unclear how the virulence of both strains compares. If MRSA were more virulent than MSSA, that would significantly affect the MIC values.

Line 304 – Please clarify what is meant by ‘bacterial adhesion’.

Line 309 – Suggestion of a possible interaction between the methyl groups on Statins and alanine groups of teichoic acids is speculative. Is there data on Statin-bacteria interactions to support this statement?

Line 321 – Binding to statins to proteins is suggested as one of the mechanisms of the inhibitory action of Statins. The readers might benefit from a table summarizing the % binding for various Statins.

Line 340-347 – Statins are electrically neutral. How do they interact with the bacterial LPS (hydrophilic) which is charged, and the phospholipid bilayer (anionic)?

Line 547-550 – It is not clear what the authors are trying to convey here.
Additional comments: I suggest the authors re-analyze the purpose and scope of this manuscript and revise this draft prior to resubmission. The purpose of the MIC analysis needs to be considered and clarified in any revisions the authors might make. A possible route to redrafting this manuscript would be to focus solely on the synergistic action of Statins with other antibiotics. This might help provide a clear framework for the review, and serve as an important resource for researchers interested in the effects of synergistic drug treatment on antimicrobial resistance.


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

Input:
Title: STATINS: ANTIMICROBIAL RESISTANCE BREAKERS OR MAKERS?
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: I consider that the manuscript has been significantly improved including all the suggestions that I made at the first round of the peer review process.


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

Input:
Title: MEASURING LANGUAGE LATERALISATION WITH DIFFERENT LANGUAGE TASKS: A SYSTEMATIC REVIEW
Review round: 1
Reviewer: 1

Output:
Basic reporting: Overall, this is a clearly-written manuscript that thoroughly describes the process of conducting a systematic review. The authors' literature search is thorough and appropriately documented with a Prisma diagram. The parameters for the review are described on osf.io.

The authors note making the R code for the forest plots available at https://osf.io/t24rv/, but when I access this link I get an error - does this need to be made public?
Experimental design: The research question - namely, how different experimental tasks affect language localization - is timely and important. I am not aware of other reviews (certainly not systematic ones) that address this topic. The methods are described in enough detail that the searches could be replicated.
Validity of the findings: The conclusions are well stated and relate to the authors' findings.
Additional comments: Overall I very much enjoyed reading this manuscript, and my lack of substantive comments is due to the excellent job you have done with the manuscript.

I did think that it would be nice to more thoroughly address the various approaches to quantifying lateralization, but i understand the rationale for putting these in a separate paper.

Other minor comments:

-It would be worth having a careful proofread of the references. In my quick glance, I noticed: some journals underlined and italicized (most just italicized); some unusual capitalization (Bmc instead of BMC, Neuroimage rather than NeuroImage); for Hickok & Poeppel (2007) I don't generally see "Opinion" included in the article title; Peelle (2012) is incorrect in the main text (Peele) but correct in the references; some citations have month included (e.g. Warrington & Shallice 1984) but most don't.

-For the Prisma diagram (Figure 1) it would be nice to include reasons for the 8 excluded articles.

-For the figshare link (https://figshare.com/articles/Forrest_Plots_of_LI_values_for_different_language_tasks/4977950), I believe "Forest" plots are mis-spelled, which might lead some people to have difficulty accessing the link. Also, if you want to share the graphs, I would suggest a smaller file size: PNG for raster-based, or perhaps a vector-based format such as .eps.


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: MEASURING LANGUAGE LATERALISATION WITH DIFFERENT LANGUAGE TASKS: A SYSTEMATIC REVIEW
Review round: 1
Reviewer: 2

Output:
Basic reporting: Well written and generally clear.
See comments under "General comments for the authors".
Experimental design: NA
Validity of the findings: NA
Additional comments: Abstract
Line 32: What does “closely matched tasks” mean? I think the authors mean tasks with baselines that actively control for as many factors as possible, isolating the linguistic process in question. This could be stated more clearly in the abstract (at this first mention of ‘closely matched’).

Introduction
Lines 83-85: “Answering such questions requires optimisation of protocols for LI measurement, to ensure that variability in LIs measured for different language functions cannot be attributed to differences in task sensitivity or measurement error.” I understand what the authors are arguing for here, but is this really even possible? How does one equate apples (e.g. language production) and oranges (e.g. language comprehension)? For instance, how does one define sensitivity without becoming circular (depending upon the LI)?

Results
Line 382: “This subtracts out non-linguistic work memory processes (see Table 3).” Probably worth noting that it subtracts out basic visual processing as well. Again, this highlights the futility of the idea of pure insertion though, as what is essentially a phonemic task, mediated via visual means (orthography), is contrasted with what is essentially a visuospatial form task.

Lines 392-397: “…a recent meta-analysis of functional imaging studies by Rice, Ralph and Hoffman (2015) suggested that while conceptual knowledge does appear to be represented bilaterally in the anterior temporal lobes, left lateralised activity was more likely when semantic content was accessed linguistically. This is in contrast to the predictions of Hickok and Poeppel’s (2007) model of language in which mapping of sound to meaning is considered as a bilateral process.”
Is this really a problem for the Hickock and Poeppel model? Doesn’t it just suggest that linguistic information is left lateralised.

Line 467: A carriage return is missing before, “Effect of ROI”

Line 545: “be” appears to be missing between “may” and “influencing”

Lines 545-546: “In this way, CTA represents a theoretical alternative to baseline tasks to subtract domain-general activity.” This is not really true as the activation analysis for any given task in a CTA still depends on the definition of a baseline.

Lines 557-559: in the references cited here (dissociated language functions within healthy individuals) I would suggest adding (though in the interests of transparency I note that I am an author on one of the papers cited below):
•	Tailby, C., Abbott, D. F., & Jackson, G. D. (2017). The diminishing dominance of the dominant hemisphere: Language fMRI in focal epilepsy. NeuroImage: Clinical, 14, 141-150.
•	Berl, M. M., Zimmaro, L. A., Khan, O. I., Dustin, I., Ritzl, E., Duke, E. S., ... & Gaillard, W. D. (2014). Characterization of atypical language activation patterns in focal epilepsy. Annals of neurology, 75(1), 33-42.

Line 566: Why would CTA be inappropriate for investigating dissociated language functions within individuals? I don’t follow the logic here – if there really is dissociation (say left Wernicke’s and right Broca’s) why should that not come up across tasks (any less so than the localisation of Wernicke’s and Broca’s in non-dissociated individuals)?

Summary and Conclusions
Line 583: the phrase “active baselines” should be qualified, along the lines of say, “carefully selected active baseline aimed at controlling for all but the language related process of interest.” I don’t think an active baseline per se is the answer the authors are proposing, but rather one that is crafted according to the language laterality question that is being addressed. I think this point is worth belabouring at first appearance in the Discussion.

Lines 588-590: “Future studies should try to more closely match task demands of word generation and sentence generation tasks.” Some further exploration of what kind of form such closer matching might take is called for here, as in some sense this is an (to use fruit as a reference again) apples and oranges question – how does one objectively identify that one has matched word and sentence generation tasks, especially once one has taken into consideration the influence of baseline too?

Lines 611-614: I still do not understand the argument that CTA is somehow inappropriate for dissociated dominance cases, any more so than for non-dissociated individuals (as per comment above). I agree that CTA collapses across inter-task processing particulars, but why this affects dissociated individuals more than non-dissociated individuals eludes me?

Lines 614-616: I agree with the sentiment that “research should focus on developing batteries of closely matched task that tap a variety of language functions to allow systematic comparisons in within-subject studies.” I think, however, that in a manuscript such as this – aimed at providing guidance to future “users” of language lateralisation approaches – that some text should be allocated to sketching out what such an approach might look like. Otherwise statements like the one quoted above just sound like empty rhetoric, rather than being instructive and useful to the reader. Inclusion of a sketch of what such a battery might look like would greatly enhance the utility of the article. As a key take home message from this review article is the importance of ‘closely matched tasks’ I think the authors are beholden to offer some more concrete suggestions here.

Tables
Table 2: ‘Verbal fluency’ should probably have a parenthetic tick in the ‘Orthography’ column, as in the case of letter based fluency (knowing, for instance, that “phlegm” begins with ‘p’ and not ‘f’). Indeed, an alternative name for letter based fluency is Orthographic Lexical Retrieval.
Similarly, ‘Phonemic judgement’ should probably have a tick in the ‘Speech motor planning’ column, given that these kinds of tasks almost invariable require some kind of subvocal rehearsal (arguably also ‘Sentence comprehension’, depending on the length of the sentence).
I happily acknowledge the subjectivity of the table (making categorical judgments about the presence/absence of a given cognition process during a given task), but these seem important constituent elements of these tasks.

More generally, I don’t think that splitting into Table 2 (functions involved in various language tasks) and Table 3 (functions involved in various baseline tasks) is necessarily the most helpful organisation in the context of the goals of the paper. The authors seem to be arguing for the use of better controlled tasks, including better control over differences between active and baseline states in fMRI (e.g. lines 175-176: “Tables 2 and 3 highlight the difficulty in designing a task which isolates a single language function in order to study its laterality”).
For the ‘wishing to be informed’ reader to make best use of this article it would seem ideal to have the same ‘cognitive function’ headings in both Table 2 and Table 3, or even better to have everything combined into one ‘mega-table’ where column one is task (be it active or baseline) and columns 2-n are the purported cognitive functions involved; then one can just scan pairs of rows to find active and baseline states that appear to isolate a given linguistic operation.
For instance, Working Memory is listed as a cognitive function in Table 3 but not in Table 2. I realise I am being a bit literal here but if I use a baseline task for which there is a tick under Working Memory in Table 3, but there is no corresponding Working Memory column in Table 2, what am I as the reader supposed to take from this? Could any deactivation that I see for the language task be due to no working memory load in the active state I have used? A mega-table would be nice in that it would enable the reader to choose a pair of rows, one active and one baseline, and compare where they did or did not have ticks and use this to identify the cognitive operation they are attempting to isolate.
Another option that could prove useful would be to have an example table that goes through the exercise of selecting active and baseline tasks. For instance, using one example language task and a range of different baseline tasks, to illustrate clearly the implications of the decisions made in task design for the observed patterns of activity (e.g. using an example from the text, an active task of sentence generation compared with either (1) a baseline that is passive fixation or (2) a baseline that consists of covert recitation of over-learned sequences like the months of the year).
I realise that these ideas are all said in text in the body of the document, but a graphical representation of the idea has the potential to render this clearly, succinctly and compellingly and I think is worth exploring. (I realise I am treading a fine line here as a reviewer, potentially straying into editorial comments, but as the tone of the article is didactic as a reviewer I would like to see a clear visual representation of the information conveyed within the body text.)

The authors seem to imply that there is a ‘true’ measure of laterality that the fMRI paradigms are trying to reveal. If laterality does vary as a function of the baseline task, which is the ‘true’ laterality, or which is the ‘clinically relevant’ laterality? Can we even know this? Implicit in some of the discussion in the paper is the idea that strong laterality is a marker of a good task, but is this really the case? If we are seeking the ‘truth’ of laterality for a given region or task, then selecting the task that has the strongest laterality might be biasing the results.
This really comes down to the question of what are we hoping to obtain through our laterality measurements? Is reliability/stability more important than strength of laterality? Or is it important, for instance, to identify what degree of laterality is indicative of redundancy of function, such that unilateral resection would be safe?
I think the Discussion would benefit from some consideration of “how do we know that we have accurately captured laterality of a region/task?”
At the least this would make overt the idea that the strongest lateralisation is the best. I admit though that this is a difficult question to answer. I just worry that the ‘strongest lateralisation is best’ approach runs the risk of relying on the metric do dictate meaning, rather than having the underlying functionality of an area dictate meaning.
Followed to the extreme, we may continue refining tasks for a given region until we come up with one that yields very strong lateralisation, ignoring those with weaker lateralisation that we tested in earlier iterations. If followed to this extreme, have we then potentially lost important information about the non-dominant hemisphere (that resecting it might cause a deterioration in function; or that resecting the dominant hemisphere might not be as disastrous as feared because the non-dominant hemisphere could support residual function)?
These are difficult questions to answer – I don’t pretend to have the answers to them. I am just urging caution with the ‘strongest LI is best’ approach, and consideration of the question regarding functional consequence of laterality measures (the difficulty of evaluating the relative utility of different LIs obtained via different tasks). It seems to me that one of the best ways to answer these questions is with surgical outcome studies. And once viewed from this light, the relevant metric would be the task for which the LI is best predictor of outcome, regardless of whether this is also the task with the strongest LIs.

===============================

In summary, I found this manuscript to be a useful summary of the literature, raising some important issues in the field. If some of the above comments could be addressed I believe this will increase the utility of the paper.


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

Input:
Title: MEASURING LANGUAGE LATERALISATION WITH DIFFERENT LANGUAGE TASKS: A SYSTEMATIC REVIEW
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript is very well written in Standard English and there are no issues with the basic reporting. Literature references and context seem to be in order. The standard article structure for systematic reviews is followed. The article does not seem to have a clear hypothesis, though, that is something the authors could potentially work on.
Experimental design: As far as I can judge it, the authors followed all standards for such studies. I do not see any issues with the design of this systematic review. The research question is well defined and meaningful. Technical standards are fulfilled and methods description is sufficient enough for potential replication.
Validity of the findings: This seems to be a very robust and statistically sound finding, and conclusions are in line with the data.
Additional comments: This is an interesting systematic reviews that covers an important question in the literature. The authors should work on clearly stating a hypothesis, but apart from that I see no problems with accepting this work.


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: MEASURING LANGUAGE LATERALISATION WITH DIFFERENT LANGUAGE TASKS: A SYSTEMATIC REVIEW
Review round: 2
Reviewer: 1

Output:
Basic reporting: ok
Experimental design: ok
Validity of the findings: ok
Additional comments: I don't see any remaining issue with the paper and think it could be recommended for acceptance now.


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

Input:
Title: THE HEAD TURN PARADIGM TO ASSESS AUDITORY LATERALITY IN CATS: INFLUENCE OF EAR POSITION AND REPEATED SOUND PRESENTATION
Review round: 1
Reviewer: 1

Output:
Basic reporting: 109: Something is wrong with the grammar in this line/sentence.
Otherwise, the manuscript is written clearly and well. The references cited are adequate.
However, see my request to add more details on the method used, rather than slavishly referring the reader to previously published methods.
Experimental design: The authors rely too frequently on citation of previous papers that have used this method to score head turning. Instead, all of the details of the method should be given in this paper.

150-151: Say what is the evidence that the calls played back are of high versus low arousal since this is critical to interpreting the results. The sentence “The stimuli were distinct with regard to the arousal state of the sender….” does not make sense. Please clarify. Also, it is not clear what data have been tested statistically.

172: Here it is stated that the head had to be held “approximately straight”. This is too vague, please give the acceptable angles of the head.

174: Say precisely what position of the ears was considered to be “straight”.
Validity of the findings: 231 and 232: What do the values n=7 and n=9 refer to here?

253 to 264: There was a significant group level bias to the left for the first 7 presentations but later it is said that the left turn bias did not differ significantly from chance. Does the latter statement refer only to the first head turn and, if so, how was a HTI value calculated?

Figure 3: Given that 7 of the 15 subjects shifted to an HTI of 1.0 in the second 7 presentations, it would be interesting to draw lines linking the score obtained in the first 7 presentations for each individual with the score for that individual in the following 7 presentations. These could then be tested using the paired Wilcoxon tests to see whether there has been a significant change at group level. Furthermore, since the data for the “following 7” look skewed, it would be better to show a median rather than a mean. Then a shift from left to right may be apparent and, at least, considered.
Additional comments: 161: Correct ‘in details’ to ‘in detail’.

310-314: This interpretation of the results of Siniscalchi et al. (2008) is most unlikely to be the case because these authors looked at habituation and chose to analyse responses to the first 7 presentations since no significant habituation of responding occurred over the first 7 presentations (see their Figure 2).

I am positively inclined towards your examination of problems with the head turning paradigm but the manuscript would have beeen improved if you had included other calls that might have given different results, especially using a wider selection of calls that might elicit low versus high arousal responses.


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: THE HEAD TURN PARADIGM TO ASSESS AUDITORY LATERALITY IN CATS: INFLUENCE OF EAR POSITION AND REPEATED SOUND PRESENTATION
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper is reasonably well written, although spelling and grammar require attention in quite a few places
Experimental design: No comment
Validity of the findings: No comment
Additional comments: This paper explores head turning in response to auditory stimulation at the individual level.  The paper addresses an interesting and understudied area and draws attention to some important potential confounders in studies on this nature.  I only have some small issues, highlighted below.

Abstract
This is well written, although inclusion of more methodological detail in places would certainly strengthen it.

Introduction
This is largely well written until the final few paragraphs, when the rationale for the study seems to become less clear.  The authors start to talk about female cats (implying a sex effect?), but it is not quite clear whether they are referring to a sex effect or the study they mention only used female animals as its subjects.  The last paragraph of the Introduction needs further expansion as it is confusing in nature and does not really set the reader up for the purpose of the investigation.

Spelling and Grammar
Line 30.  Add ‘the’ before ‘individual’
Line 31.  Add ‘the’ before ‘group’
Line 33.  Change ‘influences’ to ‘influenced’
Line 43.  Add ‘the’ before ‘behavioural’
Line 60.  Change ‘over’ to ‘to’
Line 107.  Change ‘will be….investigated’ to ‘would be…investigate’
Line 109.  Remoe ‘these’ and change ‘shows’ to ‘show’
Line 161.  Change ‘details’ to ‘detail’
Line 169.  Change ‘maximal’ to ‘maximum’
Line 171 and 184.  Change ‘to’ to ‘of’
Line 231.  Remove ‘only’
Line 270.  Change ‘on’ to ‘an’
Line 353.  Change ‘indicators’ to indicator’
Line 358.  Change ‘more a’ to ‘a more’


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: THE HEAD TURN PARADIGM TO ASSESS AUDITORY LATERALITY IN CATS: INFLUENCE OF EAR POSITION AND REPEATED SOUND PRESENTATION
Review round: 2
Reviewer: 1

Output:
Basic reporting: This has been improved.
Experimental design: No change but some extra details added. The authors' response included a photograph of the testing apparatus and that should be added to the paper itself to assist the reader in understanding the paper.
Validity of the findings: The findings are 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: THE COMPARISON OF MOLECULAR AND MORPHOLOGY-BASED PHYLOGENIES OF TRICHALINE NET-WINGED BEETLES (COLEOPTERA: LYCIDAE: METRIORRHYNCHINI) WITH DESCRIPTION OF A NEW SUBGENUS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors present a comprehensive molecular phylogeny of trichaline net-winged beetles whose taxonomic rank remains a subject of debate. The MS is written in clear English overall with minor editing (mostly grammatical) required to improve the coherence and sentence fluency (e.g., in line 131: “maximum parsimony (MP) analyses,” not “phylogenetic parsimony (MP) analyses;” and in line 136: “morphology-based phylogenetic relationships” rather than “phylogenetic morphology-based relationships”). Please also check for typos; there are still quite many, though I did not explicitly check for them. Sufficient review of relevant literature is provided and all figures and tables are prepared professionally.
Experimental design: The MS represents an original research that fits the aims and scope of the journal. The authors attempt to propose a natural classification system of trichaline net-winged beetles based on their comprehensive molecular phylogeny, together with morphological cladistic analyses at the genus level. The authors have employed a wide range of the state of the art methods with extensive sampling of molecular data. However, more detailed information and/or further elaboration on some of their analyses should be provided in Material and Methods.

- Lines 111–112: “The concatenated supermatrix was partitioned for all fragments and codon positions when appropriate.” Please provide how the final supermatrix was partitioned for each analysis. Was any software, such as PartitionFinder, used to determine the best partitioning scheme?

- Lines 113–116: Please explain why different models of nucleotide substitutions were used for ML tree search (i.e., GTRCAT) and its BS calculation (i.e., GTRGAMMA). In most cases, same model should be be used to calculate BS values.

- Lines 116–117: “The BI analysis was run in MrBayes . . . under the GTR+I+G model identified as above . . .” I highly recommend using softwares like PartitionFinder, which not only determines the best partition scheme, but also the best fitting models for each partition. The assignment of proper substitution model for each partition can significantly improve the phylogenetic reconstruction results.

- Explain how all the trees were rooted. This is essential for making assessment on monophyly of the ingroup, as well as its systematic position within the larger group (i.e., Metriorrhynchini).
Validity of the findings: The molecular phylogeny reported in the MS shows relationships among 143 samples representing 86 species of trichaline beetles, whereas the morphology-based phylogeny only include 11 terminals, each of which represents different genus within the so-called “trichaline clade.” The title of the MS, “The congruence of molecular and morphology-based phylogenies of trichaline net-winged beetles . . .,” can therefore be misleading since it sounds like the morphological analyses were conducted on the same set of samples included in molecular analyses.

Furthermore, the authors do not seem to have found strong evidence for the congruence between their DNA-based phylogeny and morphology-based phylogeny. In lines 266–271, the authors write: “The morphological analyses did not support the monophyly of the DNA-based trichaline clade. . . The deeper relationships were poorly supported,” and again in line 645: “The morphological analyses indicate different relationships,” which essentially refutes the main argument made on the congruence of molecular and morphology-based phylogenies. Therefore, a different title that more accurately describes the main finding of the MS seems necessary.

In lines 161–164: “The phylogenetic trees inferred . . . using the ML criterion and Bayesian inference were well-resolved and suggested similar relationships . . .” Please provide the BI topology as a supplementary figure and briefly discuss any discrepancy observed between the ML and BI trees, if there is any.

In lines 630–634: “The terminal position of the trichaline clade in Metriorrhynchina has already been demonstrated in the molecular analyses of Metriorrhynchini . . . Our analyses of the current more extensive dataset confirm the terminal placement of the trichaline clade (Fig. 1A).” This statement depends largely on how the trees were rooted in the present study. As I pointed out earlier, please explain in Material and Methods how your trees were rooted.

In the section Taxonomy, the diagnosis and redescription of “trichaline clade” is provided, but it is unclear which taxonomic rank this proposed clade represents. A clade can be a group of organisms at any taxonomic level, so long as the constituents are believed to be the decedents of a common ancestor. Therefore, the designation of trichaline as a “clade” does not address the main problem with alpha-taxonomy discussed in the introduction of the MS (see lines 42–43).

In Figure 1, note that there are two (B)’s in the legend and be mindful of their order (i.e., Fig.1B is the BI tree, and 1C the MP tree). Also, please clearly state that both 1B and 1C are morphology-based trees. I highly recommend collapsing all the nodes with support values below 50% in 1B and 1C trees and present them as polytomies, as already done for one of the nodes in Fig. 1C. You may provide all of the three original equally parsimonious MP trees as supplementary figures.
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: THE COMPARISON OF MOLECULAR AND MORPHOLOGY-BASED PHYLOGENIES OF TRICHALINE NET-WINGED BEETLES (COLEOPTERA: LYCIDAE: METRIORRHYNCHINI) WITH DESCRIPTION OF A NEW SUBGENUS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Manuscript is written in clear and concise English. References are ample, treated in concise format, sufficient background is provided in the intro part. Structure of the paper corresponds with usual arrangement of phylogenetic papers. Rich figures illustrates crucial structures of the morphological data, phylogenetic analyses are presented in clear and visually attractive form.

Molecular data are added as supplementary file in FASTA format. Morphological data are added as a table in the text. Probably it would be good to add it also as supplementary file, maybe in NEXUS file, to be quickly available for the readers?

Phylogenetic hypothesis is clearly formulated and correspond with text in results and discussion part of the ms.
Experimental design: The manuscript presents original biological research. Research questions are clearly formulated, corresponding with improvement in classification of the group, but also trying to link morphological and molecular data. This is highly interesting in a group developing mimetic rings, where many morphological characters have homoplastic distribution within different genera and classification based on morphology only can be highly misleading. This concept is clearly formulated in the text.

The research is rigorous, corresponds with high standards in phylogenetics, use advanced methods for evaluation of molecular data. In my opinion, it is in no conflicts with ethical standards.

Most of the methods are described in sufficient details. I have only two comments which can improve the clarity of the text:

1. Twenty species are treated as outgroup in the phylogenetic analysis. I will appreciate comments on logic how these taxa were selected – how closely related they are to the ingroup. Should be inserted in a paragraph on lines 107-122.

2. In morphological data matrix, the first taxon (Metriorrhynchus) presents probably outgroup and is used to root the resulting trees. This should be added to the text. Also, explicit information how character states were polarized should be mentioned in the text (paragraph on lines 124-142, 174-177).

List of morphological characters, included in Results (starting on line 174) should be moved in M&M section in my opinion. Some characters have detailed discussion about distribution of character states in individual genera or lineages, some have no comments. This should be unified. Several characters included presents only autapomorphies of a single genus, and bring no information to the phylogeny of genera (which is main goal of the paper).
Validity of the findings: I have no important comments to Results and Discussion parts, which are generally very well written. The following details can be however improved in the text:

Diagnosis of trichaline clade (lines 280-294). Here, on lines 286-294, you listed five very different states how male genitalia look like – this makes no diagnosis for the group! Maybe should be commented, or this part should be deleted?

Spinotrichalus, lines 427-428: “[these characters …] are the autapomorphy of S. telnovi and Spinotrichalis may be trated as synonym, when its position renders Lobatang paraphyletic.” But if you combine Spinotrichalus as subgenus of Lobatang, the same apply for the nominotypical subgenus!

The newly described subgenus, Maibrius, is characterized on lines 503-505 only as “differs from the nominotypical subgenus only in the serrate male antennae …” – but serrate/flabellate antennomeres are homoplasious within the group. You contradict this in the Discussion, lines 696-700), where you stated that “…serrate … male antennae … their value is questioned by variable morphology in related species”. Would it be possible to characterize Maibrius with some other morphological apomorphies as well?

Further, in a Remark on lines 507-513, you states that “the molecular phylogeny identified F. (Maibrius) horaki sp. n. as a genetically distant sister-lineage to other Flabellotrichalus”. But, as seen from Table 1 (lines 65-80), your sampling of this genus for molecular analysis is based exclusively on nine unidentified species (sp. A to sp. I in Table 1) from New Guinea. There is no info in this ms how many species of this genus is described, what is their geographical distribution etc. You should comment on this – why you are not able to identify your samples to species? Is your sampling covering the general distribution of known species of Flabellotrichalus – this means, is the nominotypical subgenus as proposed distributed in PNG and the newly described species from West Papua?

In the identification key, you are using exclusively male characters in some couples, but exclusively female ones in others (see lines 618-625). This is not very “user friendly”. Can this be improved? Also, info that female sex is not known for Maibrius should be inserted on lines 618-619.
Additional comments: Minor comments and typos:
line 50: “which is now a part” – it means a junior synonym or subgenus?
line 200: “1,” should be “(1)”
line 270: “Their stict consensus and one of the most parsimonious trees were unresolved” – I understand how consensus tree can have unresolved some nodes. But can be this applied also for a single parsimony three? Possible typo? Effect of missing data? This is not clear to me, please explain.
line 405: add comma
line 979: second “(B)” should be in fact “(C)”


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: SELF-EFFICACY, RELATIONSHIP SATISFACTION, AND SOCIAL SUPPORT: THE QUALITY OF LIFE OF MATERNAL CAREGIVERS OF CHILDREN WITH TYPE 1 DIABETES
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article is written in English.
The authors have used clear text.

The introduction should include more information, changes in the daily life of caregivers due to the specific characteristics of type 1 diabetes, such as glycemic control, dietary restrictions, physical exercise, and mothers' fear of The disease causes irreparable damage, hypoglycemia, etc.
It should also include a brief description of the disease (type 1 diabetes) and its psychosocial characteristics.

Therefore, the introduction is incomplete
Experimental design: It is not clear in the text the purpose of the study

I consider it important to include in the text the average age of the participants, as well as the standard deviation. Text include age of the child but no of the mothers.

Used instruments are correct, and have high levels of reliability

Methods is described with sufficient information to be repproducible by another investigator.

The time of diagnosis of diabetes in childs has not been taken into account. This variable will affect the results, It would be important to include it in the text.
Validity of the findings: The results are novel and easily replicable by other authors.
Additional comments: The study brings knowledge to science. However, it would be interesting to carry out comparisons between mothers of children with type 1 diabetes, and mothers of children with other chronic diseases, such as asthma. Studies indicate differences in quality of life between the two.


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: SELF-EFFICACY, RELATIONSHIP SATISFACTION, AND SOCIAL SUPPORT: THE QUALITY OF LIFE OF MATERNAL CAREGIVERS OF CHILDREN WITH TYPE 1 DIABETES
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article is written in English. Literature is well referenced and relevant. The authors have used a clear text and an adequate terminology.
In my opinion, the introduction of the document should raise more accurate information regarding the different typologies that exist within diabetes. Likewise, it is important to indicate in a more detailed way sociodemographic aspects that may be directly influencing the variables of self-efficacy, social support and satisfaction in relationships.
Experimental design: Research question well defined, relevant and meaningful.
Used instruments are correct, and have high levels of reliability.
Methods are described with sufficient information to be reproducible by another investigator.
I believe that one should, on the one hand, delve more precisely the aspects related to sociodemographic variables and, on the other, make clear the reasons why the application of model 1 and model 2 offer different results (lines 210-215). It is necessary to explain what rights are taken to choose one model instead of another. If we add other measures, we must explain the reason.
Validity of the findings: Results are fascinating and easily replicable by other authors.
Additional comments: This work contains very relevant aspects that confirm the tendency or relationship between levels of self-efficacy, satisfaction relations and social support of mothers caring for children with type 1 diabetes. I suggest paying more attention the psychosocial and environmental aspects that affect the variables of Study, as well as the comparison with other groups of mothers with children with chronic diseases of particular attention.


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

Input:
Title: SELF-EFFICACY, RELATIONSHIP SATISFACTION, AND SOCIAL SUPPORT: THE QUALITY OF LIFE OF MATERNAL CAREGIVERS OF CHILDREN WITH TYPE 1 DIABETES
Review round: 1
Reviewer: 3

Output:
Basic reporting: See below
Experimental design: See Below
Validity of the findings: See below
Additional comments: Thank you for the opportunity to review “Quality of life of maternal caregivers of children with type 1 diabetes and the role of self-efficacy, relationship satisfaction, and social support.” This manuscript examined differences in quality of life between mothers of children with and without type 1 diabetes, as well as the role of self-efficacy, relationship satisfaction, and social support in predicting quality of life. A strength of the manuscript include the inclusion of a comparison group. A major weakness of the manuscript is the lack of inclusion of child variables, including child age. The parents’ role in management of T1D differs greatly among very young children, school age children, pre-adolescents, and adolescents. There is a developmental transition of responsibility that occurs over time, which would certainly impact parent quality of life. Inclusion of the child’s age is needed to assist with interpretation. Other child variables such as duration of T1D diagnosis would be helpful to include as well. There are a number of additional concerns, which are described below.

Introduction
1)	Many of the references cited are over 10 years old - I recommend reviewing the introduction and discussion to ensure that this paper is placed in the  most current context, and to highlight how this paper adds to the contemporary  knowledge base.
2)	Line 76. It is unclear whether the caregiver or child experiences difficulty in emotional functioning as a result of caregiver diabetes stress.
3)	Line 80. Not all readers will be familiar with the transactional stress and coping model, so the authors should either briefly review the model or more clearly specify which elements provide a theoretical basis for the investigation and why.
4)	Line 95. It is not clear what type of relationships the authors are referring to until later in the paragraph Given that there is a body of literature on parent-child relationships/conflict in T1D, it should be made clear that the authors are referring to marital relationships earlier on in the paragraph.
5)	Line 104. It is not clear whether the authors are referring to the parent or child’s level of social support. Additionally, there is some research on social support in parents of children with T1D. The authors should review and cite this literature to expand this paragraph, which is only two sentences. See Wysocki T, Greco P. Social support and diabetes management in childhood and adolescence: influence of parents and friends. Curr Diab Rep 2006: 6: 117–122.; Lewandowski A, Drotar D. The relationship between parent-reported social support and adherence tomedical
treatment in families of adolescents with type 1 diabetes. J Pediatr Psychol 2007: 32: 427–436; Carcone AI, Ellis DA, Weisz A, Naar-King S. Social support for diabetes illness management: supporting adolescents and caregivers. J Dev Behav Pediatr 2011: 32: 581.
6)	Please explain why only the quality of life mental health domain was used as the criterion variable as opposed to the total score or other subscales.
7)	In hypothesis b, it seems as though the authors are only going to examine the regression in the diabetes group and it is unclear how the comparison group fits into this hypothesis.

Materials & Methods
8)	In accordance with people first language (see APA Manual), the term “diabetic child” should be changed to “child with T1D” throughout the manuscript. Additionally, “diabetic group” should be modified.
9)	Please specify whether there is a total score for the SF-36. Please also indicate the response format for the SF-36 and the DAS (i.e., responses range from X to Y).
10)	In the description of the SF-36, it is unclear what the domain “role-physical” measures and how this differs from physical functioning. A brief explanation is needed to assist with interpretation of findings.
11)	Line 151-153. It is unclear what “termed the reported health transition” means. Also, a citation noting similar research that excludes the single item is warranted.
12)	The Statistical Analyses section should specific which analyses were run (e.g., t tests, regression) and why.

Results
13)	The explanation of results needs further detail. It is unclear why the mother group was entered into the model when the hypothesis only specifies “in mothers of children with diabetes.”

Discussion
14)	There is a growing body of literature on sleep disruption in parents of children with T1D, which could indeed be construed as having an impact on physical functioning. This issue warrants mention and interpretation.
15)	The authors should offer an interpretation for why demographic factors were found to negatively impact certain variables.


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: SELF-EFFICACY, RELATIONSHIP SATISFACTION, AND SOCIAL SUPPORT: THE QUALITY OF LIFE OF MATERNAL CAREGIVERS OF CHILDREN WITH TYPE 1 DIABETES
Review round: 2
Reviewer: 1

Output:
Basic reporting: Suitable
Experimental design: Suitable
Validity of the findings: Suitable
Additional comments: I have read the changes made, and I can say that these reflect the suggestions made by me in the evaluation process.


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

Input:
Title: SELF-EFFICACY, RELATIONSHIP SATISFACTION, AND SOCIAL SUPPORT: THE QUALITY OF LIFE OF MATERNAL CAREGIVERS OF CHILDREN WITH TYPE 1 DIABETES
Review round: 2
Reviewer: 2

Output:
Basic reporting: .
Experimental design: .
Validity of the findings: .
Additional comments: I have read the changes made, and I can say that these reflect the suggestions made by me in the evaluation process.


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

Input:
Title: SELF-EFFICACY, RELATIONSHIP SATISFACTION, AND SOCIAL SUPPORT: THE QUALITY OF LIFE OF MATERNAL CAREGIVERS OF CHILDREN WITH TYPE 1 DIABETES
Review round: 2
Reviewer: 3

Output:
Basic reporting: See below
Experimental design: See below
Validity of the findings: See below
Additional comments: The authors did a nice job addressing reviewer feedback. I have several additional suggestions for improving the manuscript.

The additional details provided in the first paragraph are helpful; however, the types of oversight and degree to which caregivers of children and adolescents with T1D provide this oversight varies with the age of the child and the duration of diagnosis. This warrants mention. Additionally several details added are already discussed further below in the introduction and warrants them unnecessary. For example, the second paragraph is now almost entirely covered in the new details added to the first paragraph. Likewise, so is the last sentence in the second paragraph on page 4.

Additional comments regarding authors' reply to initial review points.

6)	Please explain why only the quality of life mental health domain was used as the criterion variable as opposed to the total score or other subscales.
REPLY: We have added an explanation at the end of the introduction.

Reviewer response to 6: This explanation is circular. The authors are hypothesizing that reduced QOL impacts caregiver ability to maintain good mental health. However, they are not measuring these things separately. The difference between quality of life – mental health and mental health in general warrants explanation as this seems to be overlooked entirely in the manuscript.

7)	In hypothesis b, it seems as though the authors are only going to examine the regression in the diabetes group and it is unclear how the comparison group fits into this hypothesis.
REPLY: This mistake in the hypothesis has now been corrected; it now reads “… (b) lower levels of general self-efficacy, less relationship satisfaction, less satisfaction with social support, and fewer social support providers would be significant predictors of poorer maternal mental health in mothers based on the quality of life mental health domain.”
13)	The explanation of results needs further detail. It is unclear why the mother group was entered into the model when the hypothesis only specifies “in mothers of children with diabetes.”
REPLY: Again, this mistake in the hypothesis has now been corrected; it now reads “… (b) lower levels of general self-efficacy, less relationship satisfaction, less satisfaction with social support, and fewer social support providers would be significant predictors of poorer maternal mental health in mothers based on the quality of life mental health domain.”

Reviewer response to 7 and 13: It is still unclear how the comparison group fits into the hypothesis. It is not clear if both groups are being combined to examine the impact of the stated variables on mothers as a whole regardless of whether their child has T1D. The manuscript continues to lack explanation as to why certain variables were chosen as control variables in the hierarchical regression. For example, if maternal education differed by group, then why was it not entered into the model as a control variable. Moreover, it is unclear why mother group (T1D vs. comparison) was entered as a control variable. This indicates that worse mental health was predicted by low social support, low relationship satisfaction, and low general self-efficacy regardless of mother group. However, in the discussion, the authors interpretation is unclear implies that these findings only apply to mothers of children with T1D.


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: OXYGEN-LIMITED METABOLISM IN THE METHANOTROPH METHYLOMICROBIUM BURYATENSE 5GB1C
Review round: 1
Reviewer: 1

Output:
Basic reporting: This is an interesting study with an appropriate background and rational for the study. Methods are clearly presented and as far as my experience allows appear to be appropriate for the study. In general I found the results to be clearly presented and the discussion and conclusions to be appropriate, however there are a number of areas within the manuscript that need improvement and are confusing.

My main concern is with the first three paragraphs of the results.
The first on Genomic analysis reads like an introduction and presents no new data and should be in the introduction.
The next two on Excretion products are confusing. They contain significant references to past work, are more discussion than results and as such it is very difficult to see what was achieved in this study. In particular references to Gilman et al (lines 209/212) suggest that work presented is from that study and not this.
I am sure there are results in these sections but it is not clear to the reader as presented, and needs to be significantly improved.

In the results the authors refer to growth rates, but in Table 1 and the methods talk about dilution rates, and then in Table 4 growth rates. There is nothing to say that they are the same thing, this needs to be clarified.

In Table 2 one of the columns is headed padj, what is this?
Experimental design: no comment
Validity of the findings: no comment
Additional comments: No additional comments


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

Input:
Title: OXYGEN-LIMITED METABOLISM IN THE METHANOTROPH METHYLOMICROBIUM BURYATENSE 5GB1C
Review round: 1
Reviewer: 2

Output:
Basic reporting: This paper examines a type I methanotroph Methylomicrobium buryatense 5GB1 under oxygen-starvation conditions, and used a multifaceted approach to understand its oxygen-limited metabolism. The authors reported their finding in vial experiments, continuous bioreactor experiments, RNAseq, mutant testing and flux balance analysis using a previously developed model, and compared them with previously published results on the strain and a closely related strain. The paper is well-written, well-organized and easy to follow. It provided necessary background information, and conforms to PeerJ standards.
Experimental design: This paper addresses an important question, i.e., understanding type I methanotroph’s oxygen limited metabolism, as it is highly relevant not only to understand the methanotrophs’ role in ecosystems, but also to the methanotroph-based biotechnology such as converting natural gas to valuable liquid products. The hypothesis was clearly stated, experiments well designed and carried out, with clear description on different methods.
Validity of the findings: By integrating the results from different approaches, it was concluded that M. buryatense 5GB1 maintains a hybrid metabolism of fermentation and respiration, even though a genetic potential for a full fermentative metabolism exists. In addition, it was suggested that the secretion of formate and acetate could be a response to redox imbalance. The conclusion are supported by the findings reported in the paper.
Two suggestions:
1.	Since the authors compared their results with previously published ones, it would be helpful to list the previously published ones in the table for easy comparison. For example, adding result from Gilman et al to Table 1 to provide a direct comparison.
2.	Was produced CO2 measured? I understand it is challenging to obtain an accurate measurement of CO2 in vial experiments. But it should be easier for bioreactor experiments. If the CO2 was  measured, then  it would provide more information for FBA modeling, and allow a better understanding on the carbon flux shift under oxygen limited conditions.
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: OXYGEN-LIMITED METABOLISM IN THE METHANOTROPH METHYLOMICROBIUM BURYATENSE 5GB1C
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: I am happy with the changes made by the authors


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: THE NEUROPROTECTIVE EFFECT OF NICOTINE IN PARKINSON’S DISEASE MODELS IS ASSOCIATED WITH INHIBITING PARP-1 AND CASPASE-3 CLEAVAGE
Review round: 1
Reviewer: 1

Output:
Basic reporting: The study: "The neuroprotective effect of nicotine in Parkin's disease models is associated with inhibiting PARP-1 and caspase-3 cleavage", propose to give evidence that nicotine administration can contrast cell death in the MPP+ cellular model for PD and increase PARP-1 and caspase-3 expression in the 6-OHDA mouse model for PD. They found that nicotinic cholinergic drugs may delete PD progression, in particular through α7 nAChR activation.
Besides some typos (Figure 1B in the legend, nicotine; line 231, ih), the article is written using a clear and professional English, and is supported by a sufficient literature.  However, there are several concerns for me as follows:
1.	the means and the standard errors of the mean of the data obtained are missing throughout the test
2.	it is unclear if normality and equal variance tests were run to identify parametric and non-parametric data, please specify how you choose the right statistical test
3.	representative pictures of the staining have not been inserted in fig 1, 2, and 3
4.	Could you explain why the cell death index value of the treatment MPP+ + nicotine in the figure 3A is different from the one obtained in the figure 1B? and for the treatment MPP+ + choline between figure 2 and 3B?
5.	Figure 3: please level out font size
6.	Figure 4A and D : molecular weight are missing
Experimental design: Regarding the experimental design there are two main concerns for me:
•	It is known that nicotine concentration in smokers’ body is below 100 µM (Matta et al., 2006; Clunes et al., 2008), so I wonder whether the concentration (2 mM) you used in your paper is appropriate.
•	MLA want to be used as α7 nAChR antagonist; however at concentrations > 40 nM, the MLA purchased from Tocris (as the one used) could interacts with α4β2 and α6β2 receptors. How do you validate the concentration (20 µM) that you applied?
Methods are described with sufficient details, but I ask you to specify the mouse strain used.

To further strength Lu et al findings and correlate the in vitro part with the in vivo one, I may suggest three missing experiments:
-evaluate PARP-1 and caspase 3 expression in SH-SY5Y cells in control and after MPP, nicotine, or nicotine + MPP treatments.
-quantify cell death in the striatal tissue both in the lesioned and non-lesioned hemisphere in mice injected with nicotine or saline.
-evaluate PARP-1 and caspase 3 expression in the non-lesioned hemisphere.
Validity of the findings: It is almost impossible to evaluate data strength inasmuch means have not been inserted into the text and it is unclear if data have been correctly analyzed. Moreover, some controls are missing (PARP-1 and caspase 3 expression in the non-lesioned hemisphere).
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: THE NEUROPROTECTIVE EFFECT OF NICOTINE IN PARKINSON’S DISEASE MODELS IS ASSOCIATED WITH INHIBITING PARP-1 AND CASPASE-3 CLEAVAGE
Review round: 1
Reviewer: 2

Output:
Basic reporting: Clear and concise.
Experimental design: Fine
Validity of the findings: Findings are novel and likely to be important. Links well with previous studies. Little speculation.
Additional comments: Line 301-3: I would suggest removing the following from the penultimate paragraph: “PARP-1 also plays a role in cancers, including those of the prostate and ovary, prompting the development of PARP-1 inhibitors such as olaparib as anti-cancer drugs (Deshmukh & Qiu 2015; Passeri et al. 2016).” This paragraph could be concluded by something on the importance of the sirtuin decrease arising from PARP-1 induced depletion of NAD+, with implications for mitochondrial functioning (e.g. Anderson and Maes, 2014).

It should also be noted that a7nAChR agonists are also likely to have significant impacts in PD via the regulation of e.g. the immune system and intestinal permeability (e.g. Anderson et al, 2016). This would not negate the relevance of the current results but would briefly provide the reader with a broader perspective on the role of the a7nAChR in PD.

Line 305: In the concluding paragraph, it would be better to refer to PD models and in vitro model, rather than showing “neuroprotective effects of nicotine in PD”. It is widely accepted that these commonly used PD models are poor representations of the complexity of the human condition.

Suggested references:
Anderson G, Maes M. Neurodegeneration in Parkinson's disease: interactions of oxidative stress, tryptophan catabolites and depression with mitochondria and sirtuins. Mol Neurobiol. 2014 Apr;49(2):771-83.

Anderson G, Seo M, Berk M, Carvalho AF, Maes M. Gut Permeability and Microbiota in Parkinson's Disease: Role of Depression, Tryptophan Catabolites, Oxidative and Nitrosative Stress and Melatonergic Pathways. Curr Pharm Des. 2016;22(40):6142-6151.


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: RANGE EXPANSION OF A FOULING SPECIES INDIRECTLY IMPACTS LOCAL SPECIES INTERACTIONS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors presented a well-written manuscript that meets the standards provided for basic reporting.
Experimental design: The research question is well defined and relevant, and the manuscript clearly states how this research fills a knowledge gap.  There are some details that could be included in the methods, otherwise, the methods are sound.
Validity of the findings: The data are statistically sound.  The conclusions and discussion are well stated, although the discussion could include more experiment specific comparisons to the literature.
Additional comments: The authors present an interesting manuscript examining the role that the boring sponge plays in in oyster predation by crabs.  Specifically, they investigate how the presence of absence of the boring sponge affects attach rate and handling time of the stone crab, and important oyster predator.  Although the experiment was fairly straightforward, I think this manuscript includes important information on this three species interaction.  There are a few grammatical issues, and I think the intro/discussion can be expanded.  However, I feel this issues should be easily addressed by the authors, and thus recommend publication after minor revisions. More specific details below:

Introduction: In general, the introduction does a good job putting the research in the broader context, however, I feel as though there are some specifics missing.  For instance, why use the stone crab? That is, many studies focus on blue crabs and mud crabs as oyster predators.  In fact, a number of recent studies have indicated that mud crabs are perhaps the most important oyster predator (Rindone and Eggleston 2011, Johnson et al. 2014, Carroll et al. 2015).  Interestingly, the stone crab itself is also expanding its range.  I don’t have problems with using the stone crab, but this species should be introduced in a little more detail.  Likewise, for the boring sponge, a source showing that fouled individuals are more susceptible to predation would be useful.

P 3 LN 35-38: Two small issues.  First, it is not entirely clear to me what this sentence is saying, so it probably needs to be reworded.  Second, place (1983) after Schmitt et al. on line 36, it does not need to be placed at the end of the sentence.

P 4 LN 57-59: Be careful here – this study specifically investigates how the presence of sponges impact the trophic interaction between oysters and stone crabs (Line 60-62), but not how changes in the distributions of sponges are impacting this trophic relationship.  This sentence is fine as justification, but this is not being investigated by this study.

P 4 LN 60: Here and throughout, make sure this is in past tense – “we investigate” should be “we investigated”

P 4 LN 65: Insert “than” between “survival” and “mollusks”.

P 5 LN 81-83: Were the crabs all the same sex?

P 5 LN 86: “Oysters of similar sizes were used…” What was the size range of oysters used?

P 5 LN 88-89: If the 5 hour and 24 hour oyster consumption checks were not used in the overall analysis (which it does not appear to be), this sentence can probably be omitted.

Page 6-7 LN 119-129: Make sure the model numbers here are the same as they are described in the results and the table.  In the text, model 2 is separate estimates of attack rate, whereas in Table 1 and the results, model 2 is separate estimates of handling time.

Results: The authors should delve a little more into the results for model 1, since that was the best fit and estimated different attack rates for the different oyster groups as well. While I agree that the similar support of separate estimates of handling time model (see above comment) supports that handling time is probably most important, the best model also has very different attack rates.  This should be mentioned.

Discussion: Should start narrow, then expand to broader implications.  Summarize the results of the study first, and compare to the literature.  Were the rates observed here comparable to other studies for non-fouled oysters? Which other studies of fouled oysters (or other organisms) also showed higher predation on the fouled organisms?  The discussion is ok otherwise, but I think needs to include some oyster- and sponge-specific discussion before getting into all the broader implications. Further, I think the authors should also talk about the stone crab as a range expander – it has certainly expanded its range in NC, and since boring sponges are present all along the east coast, expanding stone crabs could be problematic for oysters in Virginia, for example, even if the sponge is not in new areas there.