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

Input:
Title: SUBSTITUTIONS INTO AMINO ACIDS THAT ARE PATHOGENIC IN HUMAN MITOCHONDRIAL PROTEINS ARE MORE FREQUENT IN LINEAGES CLOSELY RELATED TO HUMAN THAN IN DISTANT LINEAGES
Review round: 1
Reviewer: 2

Output:
Basic reporting: See comments below
Experimental design: See comments below
Validity of the findings: See comments below
Additional comments: This manuscript is a follow-up paper to Klink and Bazykin 2017 GBE. Whereas the original paper used a careful matching scheme to understand how phylogenetic distance influences the relative frequencies of divergent vs. convergent substitutions, this manuscript applies similar methods to understand homoplastic substitutions to variants that are segregating in human populations and to known human pathogenic variants. In particular, the distribution of phylogenetic distances for these homoplastic substitutions are compared with the distribution of distances for divergent substitutions. The authors find that homoplastic substitutions to variants segregating in humans tend to occur at shorter phylogenetic distance than divergent substitutions and  observe a similar pattern for human pathogenic alleles. The authors attribute this pattern to changes in site-specific amino acid preferences over time and also consider a handful of specific mutations in more detail.

Overall I feel this is a well-conducted study. However, I have some suggestions for clarity and issues of interpretation that I feel should be addressed prior to publication.

Major issues:

1. The issue of ascertainment bias in the collection of segregating and pathogenic variants should be addressed in the Discussion. In particular, the database of segregating variants will miss low frequency variants, while the pathogenic variants will miss many mutations that cause lethality during pregnancy (e.g. the pathogenic variants are enriched for mutations whose effects are mild enough to permit viability but severe enough to appear in the medical literature). This means that both types of variants are likely biased in terms of the magnitude of their effects. What impact does this have on the conclusions and interpretation of the study?

2. The current analysis only considers segregating variants and pathogenic alleles that experience at least one divergent and one homoplastic substitution across the phylogeny (line 82). Looking at e.g. Table S2, this can sometimes be a tiny minority of alleles (e.g. for ATP6 only 12 out of 142 polymorphic sites are analyzed). However, this ratio varies greatly between genes and datasets.

If a large fraction of segregating (or pathogenic) variants are never substituted in other species that suggests that the preference against these mutations is consistent over time. This contrasts with the authors conclusion that site-specific preferences change. The authors should discuss the extent to which conditioning on at least one homoplastic substitution influences their conclusions.

3. Throughout, there is a lack of clarity in the language used to describe changes observed in amino acid sequences. For instant in the title it says that “Pathogenic amino acids in mitochondrial proteins more frequently ARISE in lineages closely related to human than in distant lineages.” However, this is confusing because the current manuscript deals with both segregating and fixed differences. Does “arising” mean be produced by mutation or being fixed in the population? Similar ambiguity arises throughout the MS, e.g. line 282 where alleles “emerge independently in species more closely related to H. sapiens.”

I suggest using a clear and consistent terminology, e.g. always refer to “substitutions along lineages” and “alleles segregating” rather than using alleles “arising” or “emerging” to refer to substitutions.

Minor

Line 65 — Please clarify for the reader the degree of overlap between the two datasets for both genes and sequences. Should be clear to reader that these are not independent.

Line 92-93 More detail on pairing procedure. It is not completely clear from the text how the number of samples is determined or whether the divergent and homoplastic substitutions are at the same site or not.

Line 109 “oxydase”->oxidase.

Line 255-257 This is a key sentence, but is hard to parse. Please rephrase.

Line 281-305 Passages here are highly redundant, as if there was an error in editing.


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

Input:
Title: SUBSTITUTIONS INTO AMINO ACIDS THAT ARE PATHOGENIC IN HUMAN MITOCHONDRIAL PROTEINS ARE MORE FREQUENT IN LINEAGES CLOSELY RELATED TO HUMAN THAN IN DISTANT LINEAGES
Review round: 2
Reviewer: 1

Output:
Basic reporting: See comments below
Experimental design: See comments below
Validity of the findings: See comments below
Additional comments: I thank the authors for their careful responses and think this version of the manuscript is greatly improved. I feel that all my concerns were proficiently addressed and the changes to the figures significantly improve their clarity. The expanded discussion is especially appreciated and frames this work nicely. My further comments are very minor

1)	The first table referred to in the manuscript is S4, so the ordering of materials in the supplemental should be changed.

2)	Line 352 includes a typo of the word ‘it’.


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

Input:
Title: SUBSTITUTIONS INTO AMINO ACIDS THAT ARE PATHOGENIC IN HUMAN MITOCHONDRIAL PROTEINS ARE MORE FREQUENT IN LINEAGES CLOSELY RELATED TO HUMAN THAN IN DISTANT LINEAGES
Review round: 2
Reviewer: 2

Output:
Basic reporting: See General Comments
Experimental design: See General Comments
Validity of the findings: See General Comments
Additional comments: The revised manuscript is substantially improved. The authors have fully addressed my concerns from the previous round of reviews, and I feel the manuscript is now suitable for publication. I also feel that the added background information in the Introduction and Discussion on patterns in the temporal structure of compensated pathogenic deviations will be helpful to the non-specialist reader. The new analysis and discussion of heteroplasmic-only variants (presumed loss of function) is also interesting, and I found the discussion of the relative frequency of loss of function versus quantitative impairment to be quite helpful. In particular, this provides a reasonable hypothesis to account for the qualitatively different patterns of evolution found in previous studies.


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: ARTIFICIAL NIGHT LIGHT ALTERS NOCTURNAL PREY INTERCEPTION OUTCOMES FOR MORPHOLOGICALLY VARIABLE SPIDERS
Review round: 1
Reviewer: 1

Output:
Basic reporting: I enjoyed reading the article of Yuen and Bonebrake. I found it well-written, clear and sound. The authors tested the possibility that artificial light at night could disrupt the hunting success of weaver spiders, which usually hunt by luring flying insects into their webs by means of colour attraction, mimicking with their yellow colour the appearance of flowers. They predicted reduced hunting success under artificial light at night. I found the interpretation of results sound, well-founded and well-referenced. I have however several remarks about the experimental set-up and the description of the methodologies used, which should be addressed clearly for this article to be acceptable for publication.
Experimental design: Generally, the description of the light measurements is very poor. In particular:

1) When were the measurements done? Which days of the experiment, and at what time?
2) Was light intensity measured only once per site, or repeatedly? This is important to understand as repeated measurements can reduce the influence of other environmental variables on the results (cloud cover, temperature, etc).
3) The authors mentioned the light type used, but do they know anything about the actual wavelength? Was this ever measured?
4) Similarly, what was the exact light intensity measured at each experimental web?
5) It is unclear what the variable "light" exactly represent in your models. Is this the actual light intensity or is it a categorical variable (light-control)? If the latter, why not incuding the actual light intensity as a predictor?

I further think that you should recognise and emphasize in the discussion that the results, although significant in some cases, are based on are relatively low sample size.

Also, it would be good to know something more about the species you used in terms of:

1. Is there anything know about the spectral sensitivity of this spider species?
2. You mention (L81) that this species hunt both diurnally and nocturnally. Is there anything know about its actual circadian system? It sounds as if it possesses a very flexible circadian rhythm, which might actually be beneficial in the context of light pollution if they could switch to a more diurnal hunting style. The important of knowing more about circadian rhythms in such a species, and its sensitivity to light, might be stressed more, with some relevant literature added (Gaston et al 2013 Biological Reviews, Dominoni et al 2016 Biol Lett, Davies et al 2013 Global Change Biology).
Validity of the findings: As stressed in the previous box, more details on the methodologies and background on the species in terms of light sensitivity and circadian rhythms could be beneficial to the overall quality of the paper.
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: ARTIFICIAL NIGHT LIGHT ALTERS NOCTURNAL PREY INTERCEPTION OUTCOMES FOR MORPHOLOGICALLY VARIABLE SPIDERS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The study is very interesting and addresses questions on a hot topic in ecology. I enjoyed how the background knowledge is presented in the introduction and how the authors justify the relevance of the questions they address. Also literature is properly cited and relevant. Description of the figures is good, as well as the labelling, nevertheless I would improve them, but see my comments on the following sections of the review. The manuscripts is written in proper English and well comprehensible and the data are supplied.
This said, I have some major issues that, I think, justify my recommendation for the editor.
Experimental design: I find the study novel, relevant and interesting and I like the design which is also well described. The investigation has rigorous principles but I see important issues, both conceptual and methodological, that undermine the result interpretation and the main conclusion of the study.
Firstly I want to make sure that the authors considered few points that are not mentioned in the manuscripts but are important for the relevance of the study.
1. From the data supplied I see that light intensities in the illuminated orb-webs present are highly variable. If the illumination equipment has been installed in the same manner among webs measurements should be comparable. Of course spiders can build webs in very different fashions making a standardized installation difficult, but I would have tried to standardize the illumination since the sample size is not high enough to make inference on different light conditions. Also, the light intensity detected by the sensor of the measurement device can be very different according to the angle of incidence of the light beam and the distance from the light source, potentially leading to critical bias. Did you control for it? Please provide more explanations on these points.
2. Can you consider the six sites comparable? In the manuscript it is not mentioned whether specific features of the sites are taken into account. For example moon, sky glow, light pollution coming from close by roads, cities, micro conditions around the web (bushes, branches) that could shade those light sources. Being moths highly mobile animals, overall lighting of the site might be relevant. It would be good if these conditions are standardized among sites in order to assume environmental homogeneity.
3. Overall moth abundance and activity and phenology would greatly affect your results. In my experience moth activity can dramatically vary among and within seasons depending on winter and early spring meteorological conditions (larvae development and survival), blooming of some key plant species (within season phenology), temperature, humidity and moon (within night activity). You collected data during one season, each site was sampled four (or three) times simultaneously within one night; this lead me to wonder how did you control for moth abundance and activity in your results.
4. As already mentioned, moths are highly mobile animals and can cover several kilometres in a single night. I therefore ask the authors to justify the independence of the spiders you selected within a site. Albeit I believe that the light treatments do not affect the light conditions of the dark treatments, I am afraid that moth are. For example, you could detect less attracted or intercepted moths in a dark treatment because moths are attracted to the close by light treatment. On the other hand you could detect more moths on a dark treatment because moths are rejected by the close by light treatment. This is probably species dependent and, in order to make proper inference, you need to ensure independence.
Validity of the findings: The validity of the findings are undermined by two types of issues: statistical and biological. Concerning the statistical part:
1. the sample size is certainly low and there are no replicates within sites. To make proper inference a higher N and replicates are desirable, for example by sampling the same spiders several nights, looking for more spiders within the same site, increasing the site number and repeating the data collection over two or more years. This point is linked to point 3. in the previous section of this review where I stated the need to control for moth activity among and within season. It is often very difficult to achieve a satisfying sample size in a field study, and if sites can be considered as homogeneous I think that it should not be an insurmountable problem. However, this is a weakness of the study and might seriously undermine the robustness of your results.
2. Spider size is modelled as a quantitative variable but visualized (in figures 1 and 3) and discussed as a categorical. This makes things even harder to understand and interpret. Also, the body size threshold that splits between small and large spiders is arbitrary and this should be stated in the text, or justified otherwise. I am wondering how the results change if the authors model the variable spider size as a categorical with two levels (small and large).
3. When dealing with quantitative variables (size, light intensities, attraction and interception rates, interception efficiency) it is generally desirable to represent data with scatter plots. Consider it in your next version of the manuscript.

Beyond the lack of satisfying sample size and of some important predictors (see previous section of this review), there are important conceptual issues that I would like to highlight.
1. I am puzzled by the response variables the authors are considering, especially by the interception rate. What is the biological relevance of it? If only a tiny part of the intercepted moths are eventually captured and consumed, what is the effect of light and painting of the lure on capture rate, moth mortality and spider food intake? In other words, how can attraction and interception affect prey-predator interactions? How could this set up and the results provide clues about the actual pressure of an anthropogenic disturbance such as artificial night light on the ecological interaction the authors are considering? Please, could you specify in which treatments and sites the ten predatory events occurred?
2. Moths flying close to lit webs could avoid them because they can better detect them, resulting in reduced interception events. However, their flying pattern could be greatly disrupted by artificial night light inducing them to aimlessly fly around the lamp avoiding the spider web. On a normal, aimed movement moths might be more likely to hit a spider web. Please, mention the well known fly-to-light behaviour when you discuss your results.
3. What is the time span of the sampling? There must be a typo in line 112. If the fieldwork has been conducted during one month (between Oct 2016 and Nov 2016) I do not see additional problems. If on the other hand several months elapsed from the first to the last sampling, a time variable musts be modelled.
Additional comments: The story around this study is beyond any doubts fascinating, the topic is hot and the design cleverly conceived. However, as the authors fairly mention in the discussion, the outcome of the study is difficult to interpret and does not provide conclusive results. It gives clues about the role of the lure on the chephalothorax of Nephila pilipes and the effect of artificial night light on the phases prior to the predatory event. Unfortunately, it does not highlight changes in moths' capture rate and spider food intake making the study of poor biological relevance. Further, the low sample size leads to a poor statistical power, makes the model selection difficult, results unclear and the conclusions unsatisfying.
However, I believe that the value of the study can be enhanced. I propose that the authors provide a power test to ensure that the data support the results and that the manuscript will be rewritten in order to better explain the data. Important points that need to be discussed are the definition of prey-predator interaction and the biological relevance for the animals involved in the interaction. If available, additional data could be added: environmental measurements like temperature and humidity, characterization of the light conditions in each site. An important control would be to sample data on lit and unlit orb-web where Nephila pilipes is absent to further disentangle the role of the lure which I believe is important. Light intensities in lit treatments are relatively low if you consider what you would detect within few meters from a street lamp. Increasing light intensity you could get stronger effect of the light.

Additional comments and questions on the manuscript:
Line 90: why only females?
Line 112: typo in the starting and ending date?
Line 125: are yellow flowers a common moth food source? According to my knowledge, flowers specialized on nocturnal pollinators do not invest much on striking pigmentation and are therefore mostly whitish/pinkish. However, I am not a specialist of your study area.
Line 236: limit the conclusion to the study species or justify the extension of the conclusions to other orb-weaver spider species that might be devoid of lure.


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: ARTIFICIAL NIGHT LIGHT ALTERS NOCTURNAL PREY INTERCEPTION OUTCOMES FOR MORPHOLOGICALLY VARIABLE SPIDERS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The paper reports clearly on the methods and results of an interesting experiment.  It is well-written, with good reference to the literature and well structured.
Experimental design: The experimental design is good.
I have two points that should be added to the methods section if possible - first, at the least the manufacturer and the colour temperature (in K) or ideally, the spectral power distribution of the LED lamps used should be included in order to allow the experiment to be replicated.  If possible, the sectrum of the lights should be compared to the high pressure sodium lights used in Hong Kong that the authors are trying to replicate.
Second, the time of sunset during the study should be stated.
Validity of the findings: The data is robust and analysis statistically sound, and the conclusions are well-stated.
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: ARTIFICIAL NIGHT LIGHT ALTERS NOCTURNAL PREY INTERCEPTION OUTCOMES FOR MORPHOLOGICALLY VARIABLE SPIDERS
Review round: 2
Reviewer: 1

Output:
Basic reporting: ok
Experimental design: ok
Validity of the findings: ok
Additional comments: Overall, I like how authors have changed the manuscript in order to make their conclusions more prudent since they are based on a poor dataset. As they are now, figures better represent the data, also the map is definitely useful.


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 DISTRIBUTION AND NUMBERS OF CHEETAH (ACINONYX JUBATUS) IN SOUTHERN AFRICA
Review round: 1
Reviewer: 1

Output:
Basic reporting: I am in agreement with the authors that presence data should be made more public as this makes it easier to understand and interpret species distribution. At the same time it is also important to provide enough information so that the study can be replicated and I feel that this needs more attention by the authors. For example, the article could do with some restructuring as some of the methods are presented in the results section. It would also helpful if similar ideas are grouped together and put in the same orders (i.e. results presented in the same order as the methods). At the moment some section jump around a bit making it difficult to follow the authors' train of thought.
Experimental design: The authors have collected an incredible amount of data and it is clear that they have put a lot of time and effort into the study. However, there are some concerns regarding the extrapolation of density figures, especially as most figures used violate various assumptions incl. closure and do not account for detection probability. Also, the methods could do with more detail so that the study can be replicated (details are provided in the comments).
Validity of the findings: One of the major concerns is that no measure of precision is provided for the overall number of cheetahs and therefore more care should be taken when interpreting results and comparing these to other findings.
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 DISTRIBUTION AND NUMBERS OF CHEETAH (ACINONYX JUBATUS) IN SOUTHERN AFRICA
Review round: 1
Reviewer: 2

Output:
Basic reporting: All my comments are included in the "general comments".
Experimental design: All my comments are included in the "general comments".
Validity of the findings: All my comments are included in the "general comments".
Additional comments: I applaud the authors for this impressive work, including large amount of data and the attempt of introducing a standard methodology for assessing the range and numbers of cheetah in South Africa. As compared to previously available data on the distribution of the species, this paper provides an updated status at high resolution as well as the regional variation in cheetah densities, which is based on a rich and diverse sources of data. It also attempts to determine the possible range of the cheetah based on an assumption of negative relationship between the presence of a large predator and anthropogenic factors. I think, as such, the results presented in this manuscript are generally a valuable contribution to the science as it provides a detailed information on the range and numbers of a rare (difficult to survey) species supported with abundant and statistically elaborated data.
However, the manuscript is not devoid of some major and minor problems, which require revision or better explanation to allow the reader understand the reliability of presented results. I see three major issues:
1)	It is difficult to follow how the densities were estimated. The information to understand it step by step is available in the manuscript, but it is scattered in different places. For instance, to complete the information presented in the section of methods devoted to “density estimates” one has to look at the results and the Figure 3 to get the general idea. In the “density estimates” section a detailed approach is presented explaining that existing estimates from Zimbabwe and Kruger National Park were used to estimate the total regional cheetah population. This seems to suggest that these data were somehow used for the remaining part of the cheetah range, which is strange as the area of the cheetah presence in both Zimbabwe and Kruger is really minor relative to other populations (especially in Namibia). On the other hand, I learned from results that 14 empirical local cheetah population estimates were used, but it is unclear how all these data were combined with the Zimbabwe and Kruger data and analysed.
2)	Although I appreciate the use of the Leslie matrix for estimation of the population growth, I do not understand how was it applied to estimate population densities, and specifically to account for the persecution data. Much information is provided both in the methods, results and the supplementary data referring to this analysis, however, it is not possible to follow the complete procedure and see the results of this analysis in the manuscript. I expect a graph resulting from this analysis showing the population trend based on the relationship between the growth rate and densities, both with and without persecution e.g. to illustrate the scenario mentioned in lines 370-372.
3)	I also appreciate the authors’ efforts in trying to statistically support the “possible presence” area of the cheetah and estimating their potential numbers and densities. I understand that human related factors are generally negatively correlated with the cheetah presence. However, I also think that relying on this relationship directly is somewhat misused. There may be  both, areas where predator still occurs with relatively high densities of livestock (actually seen on the Fig. 2 and areas where predator does not occur due to other than livestock/human issues. The authors seem to understand this problem as they acknowledge this in lines 445-448. Perhaps, accounting for another factor – wild prey occurrence – would add to the reliability of this estimation, but I assume such data may be equally difficult to get at sufficient resolution. Moreover, may be I missed this info, but I didn’t see the explanation how were these data on virtual cheetah presence farther stratified into densities. Anyway, considering the low reliability of the “possible” part of the cheetah range, I would put yet more emphasis on the untrustworthy character of this part of results.
Please note, I have included a number of other comments directly in the manuscript.


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

Input:
Title: THE DISTRIBUTION AND NUMBERS OF CHEETAH (ACINONYX JUBATUS) IN SOUTHERN AFRICA
Review round: 1
Reviewer: 3

Output:
Basic reporting: no comment
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: A MOLECULAR PHYLOGENETIC APPRAISAL OF THE ACANTHOSTOMINES ACANTHOSTOMUM AND TIMONIELLA AND THEIR POSITION WITHIN CRYPTOGONIMIDAE (TREMATODA: OPISTHORCHIOIDEA)
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The MS titled “A molecular phylogenetic appraisal of the acanthostomines Acanthostomum and Timoniella and their position within Cryptogonimidae (Trematoda: Opisthorchioidea)” is a well-written, insightful examination of the position of two acanthostomine genera. I found the MS to be clear and well referenced, the data is robust and the images attractive and representative of the data. I have a few comments regarding the MS, and pending consideration of these comments I recommend this article be published in PeerJ

Major points
1)	The authors do not discuss the position of the acanthostomine genera in the phylogenetic results section, it is almost entirely discussing the associations of those sequences from GenBank. Seeing as this is the basis of the paper I think it needs to be covered in the results section.
2)	On line 193 the author mention “Only three high nodal support values (PP ≥ 0.95) from three clades”, yet later in the pargraph they mention that several other clades are support values (PP ≥ 0.95) (line 204 and 208). This needs to be clarified
3)	Lines 207-217 and 279-298 discuss clading of species based on host associations or geographical localities. I strongly recommend these be reduced and extensively edited, as these associations are not really evident in the data. No clades can be found by geography (e.g. there are species from the IWP/IP (which is almost the same thing) across the marine crypto clade that do not form any really grouping) or host (e.g. there are species from Lutjanids or Haemulids across the marine crypto clade that do not form any really grouping). It is highly likely that these clades actually represent the selective sampling or Miller et al, from which most of these sequences were generated, in that the studies focused on certain host groups (reef fishes of a few families) in certain locations (GBR/French Polynesia).

Minor points
Line 15, et al: I think the authors need to make sure they say (at least a few times) that It is partial 28S rDNA, as only 880ish bases (Domains 1-2) of the region were sequenced

Line 19: “paraphyly of the genera Acanthostomum and Timoniella acanthostomines” makes it sound the like genera are paraphyletic. I would change to “paraphyly of the Acanthostominae”

Line 20: change “by itself” to “alone”

Line 46: change to “1) a terminal oral sucker; 2) a body armed with a single row of spines; 3) a preacetabular pit; 4) a genital pore that is not in preacetabular pit; 5) a seminal vesicle that is coiled posteriorly; and 6) a sucker-like gonotyl.”

Line 53: comma after Cryptogonimidae; change to “by few, and often trivial, characters”

Line 60: remove comma after “astorquii)”

Lines 57-74: Some of this paragraph should be moved to the Methods section, it is not an introduction to the subject

Line 84: “hydrobiid snails of P. coronatus” to “snails of P. coronatus (Hydrobiidae)”

Line 86: “The snails” should be “Snails”

Line 90: “As for” should be “For”

Line 94: “were” should be “have been”

Line 100: change “trematode species from the same fish host, Crassicutis cichlasomae” to “trematode species, Crassicutis cichlasomae, from the same fish host”

Lie 105: “The identification to genus level for both Timoniella and Acanthosthomum is certain based on metacercariae morphology” should be changed to “Reliable identification to genus level is possible for both Timoniella and Acanthosthomum based on metacercariae morphology”

Line 107: “questioned” should be “questionable”

Line 108: “metacercarian” should be “metacercarial”

Line 124: insert “fragment” after “ITS1–5.8S–ITS2”

Line 148: “with Bayesian” should be “by Bayesian”; add “analyses” after “(ML)”

Line 149: change “The ML was” to “ML analyses were”

Line 151: change “The BI was” to “BI analyses were”

Line 169: delete “those of”

Line 203: change “acanthostomines form a paraphyletic group” to “acanthostomines are paraphyletic”
Line 204: delete “with Acanthostomum and Timoniella not clustering together”. This is superfluous

Line 224: change “…2016). The…”to “…2016), and that the…”

Line 227: change “It’s indicate that” to “This indicates that”

Line 229: “an appropriate”

Line 232: “separate” is implied. Delete.

Line 251: I could put the genus names in full here, seeing as the are both C.

Line 254: Maybe the authors mean “from freshwater regions”, they just noted that C. urophthalmuscan tolerate brackish water so all records can’t be from “only freshwater fishes”

Line 257: change “Acanthostominae was a freshwater group that was sister to the remaining” to “Acanthostominae were sister to the remaining”. As the two genera represented independent lineages, you cannot say “freshwater group”

Line 260: Cryptogonimidae is misspelled

Line 271: add comma after “infection”; change “e.g.” to “i.e.” as you list all 12

Line 273: is the “?” meant to be in this species name

Line 305: “arisen” rather than “arise”

Line 311: “suggested” rather than “suggest”

Line 314: delete “would”

Figure 2: What do the larger black circle inside the nodes indicate?

Table 1: the species name in the second line of table needs to be italicized

Other trees: why are the species not “cf.” in these trees


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

Input:
Title: A MOLECULAR PHYLOGENETIC APPRAISAL OF THE ACANTHOSTOMINES ACANTHOSTOMUM AND TIMONIELLA AND THEIR POSITION WITHIN CRYPTOGONIMIDAE (TREMATODA: OPISTHORCHIOIDEA)
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: This is a well-written and presented paper describing the relationships of species of Acanthostomum and Timoniella to other previously reported cryptogonimid genera for which comparative molecular data is available.

The methods used for molecular characterisation of the cercariae, metacercariae and adults reported here are appropriate and sufficiently detailed.

Overall, this is a solid paper and I have no major issues with the work presented.

However, I do have some minor comments and edits that the authors should address prior to publication. I have included these as annotations and comments on the pdf file of the manuscript.


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

Input:
Title: MEASUREMENT OF SEDENTARY BEHAVIOUR IN POPULATION HEALTH SURVEYS: A REVIEW AND RECOMMENDATIONS
Review round: 1
Reviewer: 1

Output:
Basic reporting: I would like to thank the authors of this manuscript for a very interesting study. The topic of sedentary behaviour in population health surveys is very important and it is very suitable for the scope of this journal. Sufficient background and context was provided. However, more information can be added in several paragraphs to make the manuscript more clear for the readers.
Line 67) Provide citations
Line 189) "Figure 1 provides results of the search strategy used to identify 35 papers that examined the validity"… This is not very clear. Do you mean Figure 1 provides results of the search strategy used to identify [37?] papers that examined the validity?

In addition, figure 1 can be used to breakdown the number of included papers undergone psychometric testing in a pediatric population, and in the adult population.

For figure 1, it is recommended to provide reasons for excluding articles at full-text screening and the number of articles that are excluded for each reason. Please see “Item 17: Study selection Give numbers of studies screened, assessed for eligibility, and included in the review, with reasons for exclusions at each stage, ideally with a flow diagram http://www.bmj.com/content/bmj/339/bmj.b2700.full.pdf “ . Since this study is not a systematic review, this is not a serious issue. I just wanted to mention it.

In Supplemental_Table_2
Line 184) The reliability and validity of individual questionnaires (n=34 or 37?) has been summarized in Supplemental table 2. Also, I found it to be a bit confusing to know which papers have been discussed in the previous systematic reviews [16, 17] and which ones you are investigating in this study. It would be great if you could clarify.

Supplemental table 3 is not reference anywhere in the manuscript.
Experimental design: In order to conduct a comprehensive search it is very important to include mesh terms in the search. It is impossible to come up with a comprehensive list of search terms. Mesh searching will assist with retrieving all potential articles relevant to a topic. For example, as a Subjective measurement term, one might use self-rated instead of self report. By searching for "Self Report"[Mesh], you can reduce the risk of missing that specific article. I strongly suggest adding the following mesh terms: "reproducibility of results"/ OR validation studies as topic/  Validation Studies/

Mesh searching becomes even more important if you limit the search to tw field.
"The Text Word (TW) index is an alias for all of the fields in a database which contain text words and which are appropriate for a subject search. The Text word index in Ovid MEDLINE (R) includes Title (TI) and Abstract (AB)". (from http://ospguides.ovid.com/OSPguides/medline.htm#TW ) basically tw exclude searching the author's keywords field and mesh field.

One of the main limitations of this study is the lack of a comprehensive search. I think it would be great to mention this in the article to increase transparency.

Line 123) I do not think searching ‘EBM Reviews - Cochrane Database of Systematic Reviews’ would have been useful as the authors were aiming to find original research articles rather than systematic review articles.
Validity of the findings: As mentioned before one of the main limitations of this study is the lack of a comprehensive search. I think it would be great to mention this in the article to increase transparency.
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: MEASUREMENT OF SEDENTARY BEHAVIOUR IN POPULATION HEALTH SURVEYS: A REVIEW AND RECOMMENDATIONS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall a well conducted review.  Some stylistic suggestions are made in section 4 General comments.
Experimental design: Methods are appropriate.

Given there were two recently published systematic reviews that summarized the psychometric properties of sedentary behaviour questionnaires in children and youth, I suggest the authors restrict their paper to adult questionnaires.  This would make the tables and text somewhat more manageable.  There is little benefit to generating a third systematic review on the same topic (so soon as the first two).
Validity of the findings: No meta-analysis or statistical synthesis applied.  Narrative description of surveys and their psychometric properties only.

The narrative description of results provided in the text is too vague.  Statements such as ‘Computer and/or video game time were also frequently assessed’ (line170) should be quantified by including the number of studies and percentage.  Another example is ‘Many, but not all, of the surveys’ (line 173).

Despite the authors stating that they included questionnaires listed on the Sedentary Behaviour Questionnaire list compiled by the SBRN, there appear to be a number of questionnaires missing, e.g. the Bouchard Physical Activity Questionnaire, the SIT-Q.  The Bouchard Physical Activity Questionnaire link from the SBRN site goes to an Am J Clin Nutr article behind a paywall, so this could not be further interrogated easily.  The SIT-Q validation paper in BMC Public Health appears to meet the criteria for this review, so it’s not clear why this questionnaire was excluded.
Additional comments: Introduction
lines 63-65  the authors suggest that evidence supports the idea that different types of sedentary behaviours have different health effects.  This is not impossible, but differences in associations with health outcomes are probably a reflection of differential measurement error and/or confounding, rather than different physiological adaptations to sedentary behaviour in different settings.

line 75  providing readers with information to support future survey development.  Given the plethora of surveys already in existence, do we really want more?  Perhaps it would be better to suggest that better psychometric testing and refinement of existing measures be undertaken.

Methods
line 118  suggest removing the word “Unfortunately” from beginning of sentence.

Results
Throughout the text the ICCs are reported in a non-uniform fashion.  Ideally, the ICC and 95% CIs should be given.  In some places the authors simply give the ICC (eg 228), in others it appears to be the CIs only (eg line 242).

The first sentence of the paragraph beginning on line 284 is not well worded.  I think the authors mean to say something like “validation studies have looked at both single-item estimates of sitting time, or have generated a composite score from a number of items to estimate total sedentary behavior”.

Discussion
Again, on line 313 the authors note that there seem to be positive health associations for reading (compared to the negative associations seen for other sedentary behaviours).  Be very careful with the description and interpretation of this – likely to be confounding, not an actual different physiological adaptation.

Lines 325 – 326:  this sentence is unfinished.

Line 341:  actually, a number of questionnaires assessed the validity of screen time, reading and sedentary transportation (SIT-Q; SIT-Q-7d).  Do the authors mean “examined the criterion validity”?

Line 351:  confounding concept again.


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: MEASUREMENT OF SEDENTARY BEHAVIOUR IN POPULATION HEALTH SURVEYS: A REVIEW AND RECOMMENDATIONS
Review round: 2
Reviewer: 1

Output:
Basic reporting: I have no further suggestions.
Experimental design: I have no further suggestions.
Validity of the findings: I have no further suggestions.
Additional comments: Thank you for responding to all my comments. I have no further suggestions.


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: MEASUREMENT OF SEDENTARY BEHAVIOUR IN POPULATION HEALTH SURVEYS: A REVIEW AND RECOMMENDATIONS
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors have taken the reviewers' comments on board and done a decent job in revising their work.  The manuscript is generally well written.
Experimental design: No comment
Validity of the findings: Original comment:  Despite the authors stating that they included questionnaires listed on the Sedentary Behaviour Questionnaire list compiled by the SBRN, there appear to be a number of questionnaires missing, e.g. the Bouchard Physical Activity Questionnaire, the SIT-Q.  The Bouchard Physical Activity Questionnaire link from the SBRN site goes to an Am J Clin Nutr article behind a paywall, so this could not be further interrogated easily.  The SIT-Q validation paper in BMC Public Health appears to meet the criteria for this review, so it’s not clear why this questionnaire was excluded.

Revised comment:  The authors have given a satisfactory response in relation to the Bouchard PAQ, however, they do not seem to appreciate that the SIT-Q and SIT-Q-7d are different questionnaires.  The SIT-Q is (the original) domain-specific questionnaire with a past year recall period.  It's development and psychometric properties are published here:

Lynch BM, Friedenreich CM, Khandwala F et al. BMC Public Health. 2014 Sep 1;14:899.

The SIT-Q-7d is a revised version that has changed the recall timeframe to 7 days.  This version also removed some of the original items and added others (specifically relating to snacking):

Wijndaele K, DE Bourdeaudhuij, Godino JG et al. Med Sci Sports Exerc. 2014 Jun;46(6):1248-60.

Both questionnaires should be included in this review.
Additional comments: Original comment:   Throughout the text the ICCs are reported in a non-uniform fashion.  Ideally, the ICC and 95% CIs should be given.  In some places the authors simply give the ICC (eg 228), in others it appears to be the CIs only (eg line 242).

Revised comment:  Restricting the reported findings to ICC only is problematic.  The reader cannot draw meaningful conclusions or make an informed evaluation about the psychometric properties of the questionnaires based on ICC alone.  I suggest the authors contact the researchers who have published their validation studies without 95% CIs and ask for these data to be supplied for the review paper.  After doing this, please include 95% CIs where these are available, and in the case of non-response from original authors please indicated that 95% CIs are not available in your review paper (e.g. by writing something like "for TV viewing time the XXX questionnaire demonstrated reasonable convergent validity ICC=0.68, 95% CI not reported."


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: MEASUREMENT OF SEDENTARY BEHAVIOUR IN POPULATION HEALTH SURVEYS: A REVIEW AND RECOMMENDATIONS
Review round: 3
Reviewer: 1

Output:
Basic reporting: N/A
Experimental design: N/A
Validity of the findings: N/A
Additional comments: Thank you for revising the manuscript and including the CIs for ICCs where these were available.  This strengthens the reporting and will ensure readers utilising this review correctly cite the reliability and validity outcomes for the measures reported.

Thank you also for including the adult questionnaire previously omitted (the SIT-Q) in the Table.  However, I note that none of the SIT-Q findings have been incorporated into the text.  I think it is important to do so, as this questionnaire demonstrates very good ICC for TV (0.84, 95% CI: 0.75, 0.90) but poor computer ICC (0.31, 95% CI: 0.07, 0.52).  It is also one of the few measures that reports sitting during transport.


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: CRANIAL OSTEOLOGY OF THE PAMPATHERE HOLMESINA FLORIDANUS (XENARTHRA: CINGULATA; BLANCAN NALMA), INCLUDING A DESCRIPTION OF AN ISOLATED PETROSAL BONE
Review round: 1
Reviewer: 1

Output:
Basic reporting: This is a clearly written and exquisitely illustrated manuscript. I believe that there is no need of additional materials besides the informations provided in the tables and figures. I have only minor suggestions and commentaries on certain parts of the manuscript that I have included in the attached annotated PDF file.
Experimental design: This is a well-organized and much needed in depth description of a representative of one of the most interesting groups of fossil cingulates. The results have clear implications for the understanding of the taxonomy and phylogenetic relationships of pampatheres (as well as for other cingulates), and might be useful in future cladistics analysis. The bone-by-bone descriptions are very lengthy at places, but overall there is no excessive details. In fact, I should say that similarly detailed up to date descriptions are lacking for several groups of cingulates. That being said, I suggest that some descriptions may be shortened by reducing or excluding morphological features that are common to all cingulates wherever possible.
Validity of the findings: The findings reported in the manuscript are sound and they can be easily checked by any interested reader with the help of the excellent illustrations.
Additional comments: I have no additional comments in addition to those stated above


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

Input:
Title: CRANIAL OSTEOLOGY OF THE PAMPATHERE HOLMESINA FLORIDANUS (XENARTHRA: CINGULATA; BLANCAN NALMA), INCLUDING A DESCRIPTION OF AN ISOLATED PETROSAL BONE
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper is clear and very well-written; I've noted a few typos in the attached annotated PDF.
The literatures references are up to date, and well-cited throughout; I've just made a few suggestions in the annotated PDF, though these additions are not necessary.
The article is very well structured and the figures are generally excellent. As this constitutes an extensive description of cranial anatomy, I feel that some more features described in the text should be labelled on the figures (these are specified in the attached PDF).
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Overall, I found this work (a thorough description of the external cranial anatomy of the pampathere Holmesina floridanus) to be very well executed and very valuable. It will certainly count as a major reference concerning cranial anatomy in fossil cingulates and will be much used as a comparative basis. The quality of the anatomical observations and of the figures is very high.
I have only minor comments for improvement:
1) additional labeling is needed on several figures
2) comparison of cranial anatomy with a chlamyphorine and/or tolypeutine armadillo is also desirable, given the fact that pampatheres, supposedly close to glyptodonts, may in turn be close to chlamyphorine and tolypeutine subfamilies (according to DNA studies);
3) for some features with high variation (eg, teeth outline), it might be interesting to discuss whether or not ontogeny (eg, tooth wear) may explain the observed differences
4) the discussion on taxonomic ranks attributed within Cingulata (family or subfamily) should be mitigated and existing phylogenetic arguments for having two basal families of cingulates should be given better consideration
Please see further details and other minor comments in the attached PDF


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

Input:
Title: CRANIAL OSTEOLOGY OF THE PAMPATHERE HOLMESINA FLORIDANUS (XENARTHRA: CINGULATA; BLANCAN NALMA), INCLUDING A DESCRIPTION OF AN ISOLATED PETROSAL BONE
Review round: 1
Reviewer: 3

Output:
Basic reporting: Im not an american speaker so I can't check the grammar.
The scientific terms used are actualized and in agreement with the modern terminology of mammals anatomy.
The list of references is adequate, although  suggested to quote a few more for specific topics (comments on the text).
The article structure, figs, and tables are adequate. The Figures are fantastic and well planed according to the paper.
The submission is Self-contained. Its a solid manuscript.
Experimental design: This research fills an important gap in the knowledge of xenarthran anatomy. Research questions are well defined and relevant. The investigation was conducted in a very high quality way.
The methods are adequate  for this kind of research, although I suggested to explain some of them a little bit more (comments on the text).
Validity of the findings: This paper is an absolute novelty for xenarthrans anatomy.

The data is robust for this kind of anatomical paper.

The discussion and conclusions are well stated.
Additional comments: Was a placer to read this paper.
Most of my comments tried to make the anatomical part of this paper even more informative for a frequent user of this kind of papers.

I made most of the comments on the manuscript.

Most of them refers to little details that in such a long description is usual to find. I suggested to take a look of some non quoted references that I think will improve the quality of the paper (comments on the text)

I specially recommend to check with other published armadillos phylogenies (see comments on the text) if some of the characters consider here as synapomorphies, were discussed of described by other 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: SPECIES DIVERSITY AND DRIVERS OF ARBUSCULAR MYCORRHIZAL FUNGAL COMMUNITIES IN A SEMI-ARID MOUNTAIN IN CHINA
Review round: 1
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The authors explored the species diversity and composition of soil arbuscular mycorrhizal fungi communities in a semi-arid mountain – Taihang Mountain. They sampled soils from four habitat types, i.e., agricultural arable land, artificial forest land, natural grassland, and bush/wood land, and used the high-throughput sequencing with MiSeq for arbuscular mycorrhizal fungi. The sequencing depths are sufficient for arbuscular mycorrhizal fungi, and the statistical analyses are robust in detecting the important factors for arbuscular mycorrhizal fungal diversity and community composition. I only have minor comments to make it clearer.

Indicate “Taihang Mountain” in the abstract.
Did you sample the soil along elevations? As you mentioned the “mountain” in the title, please explicitly consider “elevation” or “temperature” as an explanatory variable in explaining diversity and community composition.
Figure 1, 2. Add soil types for replicated samples in figure legend or figure so that readers could understand the figure without referring to the main text.
In figure 3, taxonomic information for these 50 OTUs will enrich the information to readers.
Table 2. Make clear what kind of “results” you presented.
Table 1, 2. What the letters (A, B, C) mean?

Jianjun Wang
Nanjing Institute of Geography and Limnology, CAS


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: SPECIES DIVERSITY AND DRIVERS OF ARBUSCULAR MYCORRHIZAL FUNGAL COMMUNITIES IN A SEMI-ARID MOUNTAIN IN CHINA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper is well structured, overall the language is correct but several corrections lust be made. The literature cited is sufficient, recently updated and in accordance with the context of the paper. The pictures, figures and tables are correctly done and there was no overlapping of information. The discussion is mostly based on own experimental data, but further elaboration of own results and literature is needed regarding the effects of water content, and available P and K on AMF communities.
Experimental design: No comment
Validity of the findings: The discussion is mostly based on own experimental data, but further elaboration of own results and literature is needed regarding the effects of water content, and available P and K on AMF communities.
Additional comments: Further elaboration on the effects of most important environment factors on AMF community is needed, and some language corrections are needed. Some language corrections are suggested  in the text.


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

Input:
Title: COMPLETE GENOME SEQUENCE AND COMPARATIVE GENOMICS OF THE GOLDEN POMPANO (TRACHINOTUS OVATUS) PATHOGEN, VIBRIO HARVEYI STRAIN QT520
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors describe the genome of a newly isolated strain (QT520) of Vibrio harveyi, and compare it with related Vibrio harveyi strains. The genome sequence of V. harveyi QT520 will be of interest to the scientific community and may lead to a better understanding of its pathogenicity. However, the manuscript is very poorly written; the quality of written English is unacceptable in several occasions and is not suitable for publication unless extensively edited.

* Several sections require language edits, including but not limited to:

- Line 29: “consists two circular chromosomes”
- Lines 34-35: “suggesting strain QT520 were provided with the capacity for a highly virulent phenotype”
- Line 41: “and first compared the genome with other V. harveyi strains”
- Line 152 “This bacterium was a Gram-negative, aerobic”
- Line 158 “Chromosome I was detected of 3211 ORFs”
- Line 161 “Chromosome II was contained of 2044 ORFs,”
- Line 326 "Strains QT520 were exhibited resistance to tetracycline and ciprofloxacin"

* Figure 2: Both A and B are labelled Chromosome I and should be changed

* Figure 4B legend missing genome name

* Table 1 is missing details of Illumina sequencing technology and related assembly methods

* Sequence data is available in public domain but the size of the chromosome and plasmids mentioned in the paper do not match with that in GenBank, examples including but not limited to:
	-  Line 156 - “chromosome I of 3571617 bp”; Chromosome 1 in GenBank (CP018680.2) is 3560044bp
	-  Line 156 - “plasmid p1 of 124998bp”; Plasmid 1 in GenBank (CP018682.2) is 113574bp
Experimental design: The Phylogenetic Analysis section lacks credibility and fails to provide an accurate picture with respect to the phylogenetic position of Vibrio harveyi QT520. Which single copy genes were used to generate Fig 4A? While no bootstrap values are provided for Figure 4A, bootstrap values of 24 and 43 in Fig. 4C are way too low to provide any meaningful information. The authors also used different sequence alignment, tree building method and a different set of organisms for the three phylogenetic trees, which are thus not easily comparable.  In the single-copy gene tree, QT520 clusters with the other two Vibrio harveyi strains while in the 16S tree QT520 is closer to V. campbelli 1114GL than to other V. harveyi strains. Since this is the first report describing Vibrio harveyi QT520, the authors need to provide more conclusive evidence confirming isolate QT520 is indeed Vibrio harveyi. While the authors mention that 16S rRNA based trees failed to differentiate between the different strains, the statement needs to be substantiated with more robust tree building algorithm and/or complemented with whole genome average nucleotide identity (ANI) values with reference V. harveyi genomes.
Validity of the findings: * Provide more specifics on how the genomes were compared using Mummer. Include the run parameters used including cutoffs

* Line 208: Define “perfectly matched ORFs”

* Lines 210 - 213: Provide literature reference suggesting that the two core genes are responsible for multiple antibiotic resistance to substantiate the claim that QT520 possesses similar antibiotic resistance features as the other two V. harveyi strains

* Lines 218-221: Provide literature reference
Additional comments: * In the General features section, consider discussing the physiological/biochemical properties separately from the genomic information.

* In the LD50 section consider including some information comparing pathogenicity and LD50 values of ATCC 3843 and ATCC 43516 with QT520


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: COMPLETE GENOME SEQUENCE AND COMPARATIVE GENOMICS OF THE GOLDEN POMPANO (TRACHINOTUS OVATUS) PATHOGEN, VIBRIO HARVEYI STRAIN QT520
Review round: 1
Reviewer: 2

Output:
Basic reporting: The work from Tu et al. "Complete genome sequence and comparative genomics of the golden pompano (Trachinotus ovatus) pathogen, Vibrio harveyi strain QT520" is interesting work adding up to our understanding of the pathogenicity and the population genomics of Vibrio sp. Beyond doubt, it is an interesting work worth to be published. Nevertheless, several issues regarding the use of language have to be addressed and corrected prior to publication: e.g. L51-54 change to "... causing mass mortalities in aquaculture species having a major impact on the industry. Species affected throughout the world include the gilthead sea bream ... and prawn (Penaeus monodon)." L55-57 change to "...to infect many aquaculture species in China and is now considered as one of the major pathogens to the fisheries industry". This goes throughout the whole manuscript. I recommend a native speaker or a professional editor to go through the manuscript and correct syntax errors and misuse of English.
Experimental design: Line 98-100: Even though I understand what they mean, it is confusing. Please rephrase in a clear way.
Validity of the findings: Table 1 and table 3 can be moved to the supplement. Additionally, Table 1 "Sequencing_meth" was combined Illumina Miseq and PacBio; please correct accordingly.
Section Discussion Lines 250-256: Please remove completely. Does not adding anything to the scientific impact of the paper and delivers confusing messages. It is well known that different methods/techniques/approaches needed to answer different scientific questions. Moreover, even though it is clear that the QT520 strain is a pathogen isolated in China, the prevalence as a major aquaculture pathogen in China (or anywhere else in the world) is not addressed in this work and not supported by the data. Therefore, a reader should perceive it as another pathogenic strain of Vibrio harveyi, increasing our knowledge of molecular ecophysiology of V. harveyi.
Furthermore, it is highly recommended to the authors to submit the strain at least to one culture collection and make it available to the scientific community; I am confident several scientists would be interested to know how they can get access to the strain and this should be mentioned in the manuscript.
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: COMPLETE GENOME SEQUENCE AND COMPARATIVE GENOMICS OF THE GOLDEN POMPANO (TRACHINOTUS OVATUS) PATHOGEN, VIBRIO HARVEYI STRAIN QT520
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Line 71: Remove duplicate ‘a significant factor’

Lines 103 - 111 : The authors provide conflicting information about library prep and  sequencing method. Library prep was done for Illumina and sequencing was performed by PacBio RS II? Again in the results section the authors mention that sequencing was performed using a combination of PacBio and MiSeq. Please clarify..

Lines 348-49 : Remove last sentence of the paragraph


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: POPULATION STRUCTURE AND PHENOTYPIC VARIATION OF SCLEROTINIA SCLEROTIORUM FROM DRY BEAN (PHASEOLUS VULGARIS) IN THE UNITED STATES
Review round: 1
Reviewer: 1

Output:
Basic reporting: -The article is well written.
-Literature References are relevant and fits the study and within a broader field.
-The structure of the article is of good standard.  The format of PeerJ is the opportunity to provide greater detail and more in-depth discussions that may be restricted in other journals.  However, there is a delicate balance of introducing as much detail as necessary while retaining the attention of the reader.  This article is on the borderline of introducing too much detail.  For instance, is the use of Figures 1, 2 and 4 all necessary?  The underlying question is, Do the Figures and additional detail in the paper enhance the paper or create a distraction from the primary message of the study?  And while there is great detail on different analyses there is lack of depth on the Mexican population? Is this an important population and why?
-Complete study without indications of fracturing of the research to increase publication count.
Experimental design: -Well defined gap in scientific knowledge, confirms the efficacy of white mold screening nurseries through population genetics analysis and associated aggressiveness of isolates.
-Appropriate use of technologies for investigating genetic populations with that are predominantly clonal.  Identified and evaluated an appropriate phenotype of interest (aggressiveness).  Identified the limitations of the study, in that the pathogen is not host specific and may influence conclusions of the study.
-Methods would allow for an investigator to replicate the same or similar study to confirm results or develop new studies.
Validity of the findings: -Study provides novel results in the scientific field of S. sclerotiorum on dry beans an important agricultural commodity.  Potentially validates the continued use of nurseries for resistance selection in breeding and introduces a potential area of concern/focus for future research with the Mexican population of pathogens.
-Data is provided in repository: https://github.com/everhartlab/sclerotinia-366/.  Review of data available (includes: year, location, host…) indicates the opportunity for evaluation/use of data to confirm results and/or in future studies.  Statistical analysis of data was appropriate.
-Conclusions are well stated and appropriate.
Additional comments: Overall this paper did a wonderful synthesis of the topic while applying and interpreting the results with good scientific standards.  I found only one important area of correction which was in the abstract requiring the clarification of "11 states in the United States of America,...".  This is noted in the material and methods but is absent in the abstract.

From a scientific perspective, it should be noted that additional phenotypes for aggressiveness should be evaluated in future research.   The straw test is only an indicator for one type of pathogen potential and limits interpretation of the populations.  The conclusion given in this study is valid but greater resolution may have been possible with more phenotype data (and of course larger populations).  I was also interested in more interpretation/analysis as to why the Mexican population did not have MLH shared with any other regions, the absence of clarity on this is done at a loss.


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: POPULATION STRUCTURE AND PHENOTYPIC VARIATION OF SCLEROTINIA SCLEROTIORUM FROM DRY BEAN (PHASEOLUS VULGARIS) IN THE UNITED STATES
Review round: 1
Reviewer: 2

Output:
Basic reporting: Manuscript is written clearly, with appropriate references but limited introduction. Please see general comments reagrding that. The authors has clearly stated research questions, hypothesis, detailed M&M, concise results, and extensive discussion.
Experimental design: Research questions were clear and addressed appropriately in subsequent analyses. Methodology and data analyses are described with sufficient details to allow reproducibility.
Validity of the findings: Data was robust, available for reproducibility and well explained.
Additional comments: Population structure and phenotypic variation of Sclerotinia sclerotiorum from dry bean in the United States by Kamvar et al. utilized microsatellite loci to answer number of interesting questions including evaluating phenotypic and genetic diversity of S. sclerotiorum in the nurseries (here referred as natural populations since no control was used to limit disease spread) using regional differences and across different time intervals (span of nine years). In addition, the authors investigated correlation between mycelial compatibility groups and multilocus haplotypes among these populations. Introduction is a bit short and I would suggest expanding few sections (please see specific comments below). Materials and methods are precise and well written and I really appreciated data availability, including all sorts of analyses, which was refreshing. I also like the acknowledgment of shortcomings of the analyses (compound microsats example), which can be challenging to work with. Results were explained well with few exceptions that need some clarification. Overall, well written manuscript with interesting and relevant results for nursery producers/growers. As such, I recommend it for publication with minor revisions.


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: POPULATION STRUCTURE AND PHENOTYPIC VARIATION OF SCLEROTINIA SCLEROTIORUM FROM DRY BEAN (PHASEOLUS VULGARIS) IN THE UNITED STATES
Review round: 1
Reviewer: 3

Output:
Basic reporting: The paper focuses on addressing a question of the genetic diversity of Sclerotinia and addressing how this genetic diversity could be ligated to virulence and compatibility between strains.  The context provided for the paper is sufficient to state the goal of the research, and the authors show knowledge of the system and the analyses required to achieve the stated goals.  The article is sound and data/code for analyses have been made public and easily accessible.  In general, the conclusions were supported by the data, there are some points that required some clarification, but overall the research was well developed and the data is nicely presented to follow up the document.
Experimental design: The paper is one of the most extensive population studies in plant pathogens addressing questions on the structure of the population and the correlation of genetic diversity with specific traits.  The goals and research question stated by the authors were mostly addressed with the data and there are points that despite the difficulty of the question, there are good approximations to the answer.  For instance, the limited information provided by SSRs could not potentially lead correlation with phenotypic traits, therefore the authors acknowledge this, and approach the question using different statistical methods.
The methods and the analyses conducted are well explained and the authors provided all the code and data for corroborating the results.
Validity of the findings: Overall the study provides an extensive view of the genetic diversity of S. sclerotiorum in screening nurseries and commercial fields of dry bean. Despite that the question of how genetic diversity links phenotypic traits like MCGs and virulence has been approached before, the authors analyzed a large number of isolates using multiple markers and different statistical approaches to answer this question.  The result is still negative since there are limitations by the markers, and since this pathogen has reduced diversity.  Sclerotinia is soilborne pathogen and it is expected that there should be constraint populations at the geographical level, however, there is a reduced diversity suggesting little differentiation among regions.  This is addressed by the authors, where soil or contaminated plant material could have played an important role on the transmission of this pathogen.  In addition, the goal of establishing a census of the genetic diversity and its relation to aggressiveness is major task but necessary to establish a baseline for breeders to target a representative pool of the pathogen’s population.
Nevertheless, the authors go through a good job of addressing the issues and limitations of the study.   There are some points or comments that I would recommend to the authors to discuss and/or consider, those were included on the general comments.
Additional comments: •	The availability of the data and the analyses posted on github was really helpful and it made very enjoyable to read the paper and understand some of the logic of the authors, it has been a great experience.  It also provides a good view on the paper and it helps to assess paper and give recommendations on the paper.  Kudos!  I want to compliment the authors for making these resources available.

•	Since populations for certain areas were only collected within a single year, variation between years and region should also be looked at with caution.  Are year and region still important if samples with more than one year are retained? How much variability is explained if so?  It will a good way to corroborate if there is a continuum of genotypes or every year is bottleneck increasing diversity and to determine how much populations sampled once contribute to the analysis.  However, the authors are aware of this on line 350-352.

•	One thing to be addressed is how well these microsatellites represent the whole genome, this was not addressed on Sirjusingh and Kohn (2001) maybe due to the lack of the genome sequence. However, this could explain the lack of power of the existing set to represent the haplotypes in the population.  Despite, that most studies are using reduced genome approaches or more powerful techniques, it will be informative for other researchers still using this set of microsatellites to have this information.  Njambere et al. (2010; 10.1139/G10-019) did an approximation for S. trifoliorum using linkage groups, but I am not aware of something similar for S. sclerotiorum to corroborate these SSRs.

•	The relation between MCGs, MLH and aggressiveness is quite interesting, however, it is hard to follow in the text.  The graph in github (https://github.com/everhartlab/sclerotinia-366/blob/master/results/mlg-mcg.md), summarizes really well some on this information as well as table 3.  Maybe you can consider including this graph either on the article or add a column to table 3 with the average aggressiveness.  The graph might be more meaningful since you can see the variability of aggressiveness of the different strains by the different factors.

•	L384-404 The authors have a discussion on differentiation of the population based on region.  Then, the discussion is centered on how regions like WA still had a considerable amount of variation within the US locations sampled.  However, one of the points discussed is that one of the locations was inoculated in 2002 and then crop history differed between the two locations sampled.  As the authors suggested there is little or minimal differentiation between isolates from different hosts.  Nonetheless, the source of the sclerotia used to inoculated the fields is also different.  This could be also part of the differences that the authors see in 2008.  Despite that other studies have indicated a limited differentiation between hosts, it seems that there is some effect on the genetic.  Is the virulence different on these isolates with respect to other isolates? Aldrich-Wolfe et al. (2015) presents information on the allele sizes for the markers used, are these haplotypes present in the current study?  It will be interesting to determine if most haplotypes are share or not, and if those present across multiple hosts have a different virulence.  However, the major point of the paper is dry bean but the history on crop rotation could explain some of the variability across years.

•	P6L262 varaibles change to 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: EPIGENETIC CONSIDERATIONS IN AQUACULTURE
Review round: 1
Reviewer: 1

Output:
Basic reporting: The importance of epigenetics in different fields of biology including fundamental molecular biology, evo-devo problematic and more applied ecological contexts has led to a tremendous increase in the literature, urging for appropriate syntheses of the recent knowledge and perspective in the related fields. Here the authors propose a review about the 'epigenetic considerations in aquaculture' that suits the readership of the journal in my opinion. The work is divided into two parts, with the first dedicated to a short but comprehensive description of epigenetic mechanisms in the different taxa that are considered in the manuscript, which are the most important for aquaculture, fish and shellfish. Then the authors provide a clear perspective of the broad interests of application of epigenetic knowledge for aquaculture present practices and future developments.
	The manuscript is well written and the quality of the writing was really appreciated. I also congratulate the authors for bringing together data from vertebrate and invertebrate groups. This constitutes to me the strength of the manuscript and its most important contribution especially when compared to a review by Moghadam et al. in 2015 on the same topic but that 'only' considered fish.
	Nevertheless there are a few substantial comments that should be addressed before acceptance (see other sections below), mostly clarification of apparent contradiction and inclusion of recently published findings.
Experimental design: Why did the authors choose to use Google scholar to browse the literature? There are known issues with the quality/relevance/extensiveness of the results provided by this service when compared to 'classical' scientific literature databases (Lewandowsky et al. Online Information Review 2010,Levine & Gil 2009). I believe this might be due to the lack of such a unique database covering the width of the reviewed topic, especially for aquaculture journals. Please provide justification in the text.
Validity of the findings: Although the literature reviewed is mostly cited in a relevant, exhaustive and comprehensive manner, there are some places where the authors need to provide additional data, details or  explanations  of their interpretation of the cited references at the cost of what seemed to me incomplete or contradictive review.  There are two places in particular:

- Lines 201-203: ' The function of DNA methylation also appears to be similar across vertebrates with the exception of a role in genomic imprinting which is unique to mammals (Potok et al. 2013)'. In this paper, Potok et al. considered 'imprinting ' in the sense of McGowan and Martin, ie. ' imprinting results in an inability to reproduce parthenogenetically because a genetic contribution from both parents is necessary to successfully complete development.' (McGowan and Martin, 1997). However, imprinting is a broader phenomenon which is mostly considered as 'the non-equivalent contribution of the parental genomes to the embryonic genome', or 'the preferential expression of a parental epiallelle over the other'. The existence of such different contribution of parental nuclear genomes, ie imprinting, has been demonstrated in fish and is described by the authors lines 325-332 ' Using genome-wide DNA methylation profiling, authors showed that pseudomales (generated by exposing genetic females to high temperature during a sensitive developmental window) exhibit methylation patterns consistent with genetic males, both of which differ from the methylome of normal females. Excitingly, it was reported that global methylation patterns are inherited by F1 pseudomale offspring generated by crosses between pseudomales and normal females, suggesting transgenerational epigenetic inheritance of environmentally-induced sex reversal in this species (Shao et al 2014).'. Those two claims contradict one another to me. Please clarify.

- Lines 225-226 : remove '(and putative promoter regions)', which is debated and not assumable regarding the present knowledge.

-Line 336-350: Please include discussion on nutritional influence on phenotype in bivalves (broodstock conditionning....).

- The literature about DNA methylation in marine organisms has significantly increased very recently, and brings data that should be included here. importantly, please consider Knecht et al Toxicol Appl Pharmacol 2017, Burgerhout et al PloS one 2017 and Artemov et al Mol Biol Evol 2017 for the fish; Riviere et al PLoS Genetics 2017 and Gonzalez-Romero Aquat Toxicol 2017 for the oyster.

	An important issue in aquaculture is the control of the reproduction cycle of exploited species. The manuscript deals with sex determination but would gain an additional asset if presenting a short paragraph on this topic on both fish and bivalves. See for example Coveto-Solo et al. Anim Genet 2015, Zhou et al Int J Mol Sci 2016 for fishes, Jiang et al Mar Biotechnol 2015 in the oyster.

	The reference list needs format editing for homogeneity.
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: EPIGENETIC CONSIDERATIONS IN AQUACULTURE
Review round: 1
Reviewer: 2

Output:
Basic reporting: The present manuscript represents a very interesting effort in bringing together current epigenetic and marine biology knowledge. It is especially interesting the insight this work provides concerning the potential of epigenetic approaches to improve aquaculture practices. Epigenetics is a relatively young discipline, nonetheless, it constitutes the basis for most molecular biology research done in model organisms nowadays (e.g., cancer research). Still, this approach lacks development in other fields encompassing critical environmental components such as ecology, marine biology, and fisheries, just to mention some. In that sense, the present work has the potential to make a great contribution to bring epigenetics into the latter, helping improve current management, conservation, and restoration strategies.
I found the present manuscript well organized in essence, with most of the relevant literature cited as well as many gaps in knowledge addressed. That being said, I believe the work needs substantial improvements to live up to its title. If this work is meant to be a foundational reference (as mentioned by the authors at some point), it requires further elaboration on critical points, as well as additional references and contents completing the information provided.
Overall, I think this work is promising, however, I am recommending major revision before further considering it for publication in Peer J. I believe authors can improve this work substantially and I hope the comments below might help them do that in the best way possible.
Experimental design: N/A
Validity of the findings: N/A
Additional comments: Abstract: Current narrative is a bit cloudy with some awkward sentences “… has dramatically increased to where we are now able to characterize …”. Overall, my suggestion is to make abstract more descriptive of the key concepts developed throughout the manuscript.
Line 54: refeernces for Wang et al 2009, and for Wu et al. 2011, are duplicated in the references section.
Figure 1: Is it correctly represented? Why is there black and grey text? Why is epigenetics box intersecting with genetics? Why not with environment? Where are the references supporting the different markers used? These should be indicated in the figure. Please, provide a more coherent and detailed explanation of this figure.
Line 89: Survey methodology is not really appropriate as a section in the manuscript. This looks like some sort of justification in case any relevant references are missing (blame Google!). It seems a bit narrow the fact that this revision can just be based on a google search, rather than on author’s genuine knowledge and passion for the topic through the years.
Line 122: what about plants? Since general background is given here, it is relevant to mention that trans-generational transmission of DNA methylation has been observed in plants. Please elaborate.
Line 127: Histone modifications are explained here but the epigenetic role of histone variants is completely neglected? What about their role (and the role of their PTM modifications) during epigenetic regulation? This must be addressed here.
Line 133: degree in which DNA wrapped around would be probably better explained in terms of electrostatic affinity between DNA and histones?
Line 132: core histones are modified at N terminal tails, but linker histones are modified at C terminal tail, it would be better to say that PTMs occur mostly at N terminal tails.
Line 136: “These states are dependent on the type (i.e. …) since not all modification types are mentioned here, it is probably better to use “e.g., …”. There are many other less know PTMs in addition to the 4 mentioned (sumoylation, Pro-isomerization, ADP ribosylation, biotinilation …), although this is not a review about PTMs, authors should at least aknowledge that more PTMs exist.
Line 137: different chromatin states not only depend on modifications, they also depend on histone variants, extensively!
Line 139: Lawrence et al 2016 citation lacks details in the references section.
Line 141: the concept of the histone code has been losing momentum during the last few years, not sure if relevant to mention that here. At any rate, it would be interesting to at least dedicate 1 sentence to explain what the histone code hypothesis is about.
Line 144: add “among many others” at end of sentence, there are many other histone-modifying enzymes not mentioned here.
Lines 145-146: references here (except Lawrence) are a bit outdated, I suggest updating this list, some options could include
http://www.readcube.com/articles/10.1038/nrg.2016.59
https://www.ncbi.nlm.nih.gov/pubmed/24614311
Line 147: “modifications IS highly regulated …”
Line 157: “code for proteinS …”
Line 171: Information about trans-generational inheritance of RNAs is lacking, need to include that, see ref: http://www.readcube.com/articles/10.1038/nn.3695
Line 191: I am missing a reference justifying the affirmation made by that sentence.
Line 194: Same, reference at end of sentence will be better.
Line 239: There is a significant amount of knowledge about histone variants in shellfish, (see work by Jose Eirin-Lopez’s lab), since everything epigenetic seems so scarce in shellfish, I believe those are worth mentioning. Similarly, this group has recently published a paper summarizing epigenetic methods for the study of shellfish epigenetics, I’m surprised this is not even mentioned here: https://www.ncbi.nlm.nih.gov/pubmed/28848447
Line 254: Recent work has addressed the role of histone H2A.X phosphorylation on oyster responses to toxins: https://www.ncbi.nlm.nih.gov/pubmed/28315825
Line 255: Bivalves replacing histones by protamines in sperm DO NOT EXIST. Bivalves either replace histones by sperm-specific histones or by protamine-like proteins. The only molluscs with protamines in sperm are cephalopods. I suggest that authors check https://www.ncbi.nlm.nih.gov/pubmed/19708021 for additional information.
Line 278: This section is where this manuscript starts discussing topics never discussed before. This should be the strength of the present work. I encourage authors to revise and further elaborate this section of the manuscript.
Line 285: how does “developmental programming” relates to the concept of hormesis?
Line 352: would it be interesting to incorporate the concept of “assisted evolution” in the case of aquaculture? This has been described for corals, raising a lot of controversy, would it make sense in the present context?


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: IDENTIFICATION AND CHARACTERIZATION OF A NOVEL ZEBRAFISH (DANIO RERIO) PENTRAXIN–CARBONIC ANHYDRASE
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is written properly with minor misspellings and other mistakes, like activates (line 94), was taken (?)(127), no comma (135), of (165), contains (lines 514-515), and more.
The literature seems correct and well covered.
The structure of the manuscript is proper with a few logical flaws, at least from my point of view. For instance, why the "The region after the CA domain...." chapter does not directly follow the "Exon lengths..." chapter?
In many instances there are abbreviations used that are not explained, e.g. dpf, MO, hpf that can be difficult for scientists from other fields.
Overall the manuscript is interesting, produces a lot of data and partially answers the question of the function of the pentraxin domain in CA VI.
Experimental design: Experimentally this manuscript meets all criteria needed to be published in PeerJ.
The research question is well defined and it clearly aims at solving the presence of an additional domain in non-mammalian CA VI.
Experiments are well performed, however some data is missing:
1. In sequence searches there are no e-values and scores given. We don't know if there are more distant sequences that could be added to the analysis.
2. Why the sequences with only 20 aa insertions were eliminated from the analysis? Was anything else wrong with them?
3. What was the ground on which you decided to edit the longer sequences? What, except for the usual sequence length, lead you to such a decision?
4. Since both DNA and protein sequences seem very similar why did you decide to analyze both types of trees? Usually it is used for more distant cases.
5. In the manuscript you discuss almost the same frequently figures from the main manuscript and the supplemental ones. I think you should decide about that because it is quite inconvenient for the readers.
6. In the "Evaluation of potential..." part of the Methods you state the presence of a hypothetical 18 residues helix. When reading from the beginning the reader has no idea what it is and why you even mention it.
7. At the end of the "Construction of recombinant..." method you mention another PCR. Honestly, I couldn't get what this PCR is for and what is the difference from the previous one. It should be clarified.
8. In "Quantitative real-time PCR" you do not mention how many times you tried this experiment, for statistical reasons.
9. "In the "Non-mammalian CA VI..." Results section you do give details about conservation of the CA VI amino acids (xx out of yyy), but you miss it for the PTX domain.
10. In the phylogeny figures you do not mention if the sequence used is DNA or protein. It should be mentioned in the figure legend.
11. If you want to emphasize specific data from trees you may colour them accordingly.
12. At the end of the first Results chapter you state that PTX is more similar to short pentraxins, CRPs and SAPs. What is the significance of that? I couldn't really find a conclusive answer to that.
13. In the "Platypus is a candidate..." section you do not mention if you tried to fit this contig into the genome. If so where did it fit the best?
14. In my opinion th e"Light scattering analysis..." chapter should be located before the "Recombinant CA VI-PTX..." chapter.
15. Figure 7 is not too well described. Same for Fig. 8.
16. In Fig. 9 there is an inconsistency. What sequence is right: KGP or KQP...?
17. The difference between figures 9 and S6 are not well defined. It needs a better explanation.
18. Your "Conclusions" is a Summary.
Validity of the findings: This manuscript describes a novel finding and shows interesting data both in theoretical and experimental parts. The results however do not fully answer the question of the specific function of the PTX domain in the CA VI family. The hypothesis of a replaced attaching function is great and needs future analyses.
The results are sound and original and are suitable for publishing after these minor issues are fixed.
Additional comments: I lie this manuscript for its broad theoretical and experimental reach. It would be perfect with "the last thrust" that will prove the binding hypothesis. I hope you get to this point soon.


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: IDENTIFICATION AND CHARACTERIZATION OF A NOVEL ZEBRAFISH (DANIO RERIO) PENTRAXIN–CARBONIC ANHYDRASE
Review round: 1
Reviewer: 2

Output:
Basic reporting: I enjoyed reading this manuscript. Authors address the interesting case of CA6, which gained a pentraxin domain in the ancestor of vertebrates and then lost it in the ancestor of mammals (eutherians?).  This study is very thorough, and puts together high-quality phylogenetics, structural, genomics and functional studies. I recommend its publication.

There are a few questions that could be discussed. I would love to understand why this happened as it did (1st gain, 2nd loss, combination of those two domains). I know it is probably impossible to answer this kind of questions with high confidence, but at least authors could attempt to discuss possible hypotheses on why this domain combination, why not in mammals, what impact it may have had on the respective functions of the gene?

What about CA6 in mammals? A comparison may help understanding the evolutionary history of this gene. Is the loss of the domain associated to variation in sequence conservation patterns, expression of the gene across tissues, etc? According to GTEx, human CA6 is only expressed in skin. Does this provide any hint on the above questions?

It is remarkable that the amphipathic helix has been conserved in mammals (btw, I liked how authors inferred the origin of this helix). This suggests it has an important functional role. Any idea on what this role might be?

Regarding the pentraxin domain, it would be interesting to see if the patterns of conservation / divergence differ compared to other pentraxins. This may give insights on functional divergence of this domain.

In summary, this is a fascinating case for which further functional studies may benefit from attempts to answer the above questions.

Minor comments:
-Introduction, lines 87-90: I think that sentence is not needed
-Methods, lines 168-169: check grammar
Experimental design: Minor comment: the phylogenetic tree of the pentraxin domain would be easier to interpret if paralogous pentraxins from other vertebrates (not only human) were included. This is just a suggestion, it's fine as it is now.

In future follow-up studies authors may want to scan for potential signatures of positive selection associated to these domain gain/loss evolutionary events.
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: IDENTIFICATION AND CHARACTERIZATION OF A NOVEL ZEBRAFISH (DANIO RERIO) PENTRAXIN–CARBONIC ANHYDRASE
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript by Patrikainen et al., describes the biophysical characterization and bioinformatic analysis (phylogenetic and 3D modelling) of the carbonic anhydrase VI from Danio rerio.

Minor comments:

1- Regarding the 3D modelling of the amphipathic helix. Its 3D localization in the interface between CA and PTX domains is unconvincing (Figure 5).
My recommendation would be to remove it.

2- I consider it appropriate to cite the Pfam database, where
phylogenetic trees and domain architecture can be found, for example:
http://pfam.xfam.org/protein/E9QB97_DANRE
Experimental design: no comment
Validity of the findings: no comment
Additional comments: no comment