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: COMMUNITY INVOLVEMENT WORKS WHERE ENFORCEMENT FAILS: CONSERVATION SUCCESS THROUGH COMMUNITY-BASED MANAGEMENT OF AMAZON RIVER TURTLE NESTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: In general, the text is written in good English. However, there are some inconsistencies in spelling and punctuation. I have not tried to spot all of them not being a native English speaker myself. Please check the language again.

There are some inconsistencies in referencing. The authors should revise the references and make sure they are consistent throughout (e.g. chronological order of sources cited). The references themselves are well justified.

The article structure follows the PeerJ standard. Content-wise, the main weakness of the manuscript relates to how the argument is elaborated. The authors fail to provide a proper description of their case. This may be because they are too familiar with the case themselves. However, this is not an excuse for not telling the reader the necessary details about e.g. the study area social setting, the community or communities involved in the management initiative, other relevant stakeholders, the roles of different actors in the management work, etc. I have indicated these information needs in my detailed comments to the annotated manuscript pdf. Another major problem is that the readers fail to define well their key concepts. This is something I comment in more detail in the pdf, too. How are the key concepts defined and how they relate to each other in this particular study? To make the line of argument convincing and scientifically sound, the concepts and the background need to be revised.

The tables and figures are appropriate, but only if the above revisions are successfully made.

The authors provide no raw data. The editor may assess whether it is in line with the PeerJ policy in this case.

Because of the above reasons, in its current form, the manuscript is not entirely ‘self-contained,’. Its line of argument is hard to follow without knowing more about the case itself. However, I think it can be elaborated to stand alone and that it can represent an appropriate ‘unit of publication’. A major revision is needed.
Experimental design: The manuscript is a piece of original primary research. However, I am not sure how it differs from a ”case study” – something PeerJ is supposed not to publish. In my view, most studies in this field are case studies, with one or more cases involved. I assume that this type of study design nevertheless is considered to be within the aims and scope of the journal.

The paper suffers from weaknesses in the definition of its main research question(s). This mainly relates to the unclear conceptual basis and the insufficient background. Both in relation to the case itself and in relation to similar cases elsewhere. Doing this helps you to come up with well defined, relevant and meaningful research questions. This also helps you to answer how your research fills an identified knowledge gap.

The authors need to better describe their study methods and materials. This should take place along with conceptual and background revisions leading to better elaborated study questions. The field study permits as described by the authors  seem appropriate to me.
Validity of the findings: The quality of the data cannot be easily evaluated (no raw data was provided). Better data (methods) is needed.

My detailed comments in the annotated pdf show my main concerns about how the conclusion are stated, linked to original research question and limited to supporting results.
Additional comments: I welcome the paper as an interesting piece of work on an important topic. In my view, in its current form the manuscript suffers from such major weaknesses that it requires a complete overhaul (major revision) for the editor to make a decision about its publishing in PeerJ. All of my comments and suggestions are found in the attached annotated pdf of the manuscript.

As a summary, I would suggest that the authors:

1) Revise and rewrite the conceptual basis of their paper. All key concepts need to be well defined and their relationships to the elaboration of the hypotheses and the argument should be well established.

2) Elaborate a proper background section. This can be dividedf, for instance, between the intro and the materials and the methods sections. The background should deliver key information about the study area setting, the relevant stakeholders and their roles, institutional setting, the situation of the turtles including main threats, the details of the community involvement in management, and so on. I have pointed out these needs in the annotated pdf.

3) Better define the research questions and elaborate the line of argument from this to the hypotheses, the methods, the results, discussion and the conclusions. This seems quite obvious, but I think that the authors may be “too” familiar with their case – they forget that the readers most likely are not. This affects not only the line of argument but also the general interest of the paper.


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

Input:
Title: COMMUNITY INVOLVEMENT WORKS WHERE ENFORCEMENT FAILS: CONSERVATION SUCCESS THROUGH COMMUNITY-BASED MANAGEMENT OF AMAZON RIVER TURTLE NESTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The topic of this work is certainly very relevant for conservation of freshwater turtles. The comparison between enforcement and community management initiatives is highly appropriate and important, as enforcement is not sufficient (and often not effective) to control poaching of turtles and turtle eggs (and community initiatives for protection of beaches is one strategy used throughout the Amazon). That being said, I think the authors fail to provide sufficient details about the work for me to assess the quality and validity of the findings (see experimental design section).

Minor points:
Ln 49 – You do not mention all the efforts and suggestions on the demand side of the issue (e.g., target consumer behavior, increase alternative sources of food for consumers, decrease price of alternatives). You focused only on the supply side, which is not the only way to help conserve wildlife.
Ln 95 – You actually obtained ethical approval by an ethics committee. You always have to get that approval when you interview people, even if you don’t perform experiments with them. However, I missed where the data of the interviews are. You did not present these data.
Ln 165 – Are you taking the effort (liters of fuel) used for the entire region or for that portion you studied? It seems to me that if you are comparing only that portion, you should include the effort only for that portion. Is that what you did? If you used the effort for the entire region, please justify.
Experimental design: The research question is well defined, but the design of the study is not.
1- The authors only provide % of nests harvested and # of nests not harvested per year. They do not provide # of beaches surveyed, # of nest per beach per year, # of nests harvest per beach per year. Without this information, I cannot judge whether the work was rigorous or whether the finds are valid. What is the n of the study? What is the unit of measurement? The authors present % of nests harvested, but I would think that beach (or location surveyed) is the unit. If someone comes to harvest eggs on a beach, the harvest on that beach will be correlated. In this case, nest is not the sampling unit, but the beach might be (if beaches are not also spatially autocorrelated with regards to harvest – if they are, then n potentially equals 1).
2- The authors conducted sampling or census in the study area? I imagine they conducted a census as they did not use a statistical test to assess differences between the treatments. However, P. unifilis is known to nest in different habitats, not only on beaches. Did you survey all possible habitats (e.g. river banks?). Did you find all nesting habitats? I find it hard to believe that you would be able to map all nesting locations of this species, which can change from year to year. Please provide a description of your sampling/census. The authors should not expect me to read another paper to understand the basic information of sampling design they used.
3- The authors do not have a comparison/control group. I understand that sometimes it is not possible to have a comparison, but that only increases the need to be very clear about the design. What if number of nests varied widely (but naturally) from year to year? Fig 2 shows that 2011 and 2017 had higher number of nests, and the enforcement years had a small number of nests. What if the year of community management had a higher number of nests to begin with (compared to enforcement years)? You say that “Fewer nests were found during the years with enforcement patrols (2015 and 2016), and we hypothesize that these reductions can be attributed to the increased and/or more careful concealment of harvested nests as a response to the presence of the enforcement patrols” (Ln 242-244). But, if instead, the number of nests during enforcement years was naturally lower than the previous years (independent of treatment)? You don’t have a comparison to know that. Can you provide information that would address/ cast doubt on these potential confounding factors?

4- Ln 233-253 - Yes, people can conceal the harvest. With that in mind, if community members helped you to monitor harvest (Ln 152-154), then they knew exactly what you were looking for and were in the position, if they wanted to, to conceal the harvested nests better than anyone who harvested in other years. How do you know that this is not the case and that it is not why you had a lower rate of harvest? You are assuming people concealed the harvest more during enforcement years, but what if nest harvest was actually more frequently concealed during the year of community management? Then your results of % of nests harvested would be confounded with that.
Validity of the findings: 1- I cannot assess the validity of the findings without more detailed information about the sampling design.

2 – The authors concluded that “good will, understanding, and perceptions of local communities are the vital/keystone components for the success of conservation activities” (Ln 268-270). Did you measure these variables? If so, please present the data. If not, I would suggest the authors limit these claims as just hypotheses.
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: COMMUNITY INVOLVEMENT WORKS WHERE ENFORCEMENT FAILS: CONSERVATION SUCCESS THROUGH COMMUNITY-BASED MANAGEMENT OF AMAZON RIVER TURTLE NESTS
Review round: 3
Reviewer: 1

Output:
Basic reporting: No additional comments
Experimental design: No additional comments
Validity of the findings: No additional comments
Additional comments: I am happy to see that you have succesfully addressed (most of) my criticism. It was not my fault that you did not notice all of my comments in your first revision. Please understand that a proper response to all of the comments made by a reviewer is necessary -- as you know this is voluntary work and the time and dedication of the reviewer should be appreciated, even when the authors disagree on some of the points made. With the current revision (in practice the first round of changes), I think the article is much more universally interesting compared to the original version. In particular, this concerns the institutional aspects of the case. I have made seven (7) minor comments/requests in the pdf. I think you should be more careful in your use of the concept of "community" and very shortly state what your "community" is, so that the reader understands better the institutional and social logic of the interventions made. Please consider this -- it should be easy to tackle the issue with a few well chosen words added. I think this is an interesting paper and I hope to see it published 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: COMMUNITY INVOLVEMENT WORKS WHERE ENFORCEMENT FAILS: CONSERVATION SUCCESS THROUGH COMMUNITY-BASED MANAGEMENT OF AMAZON RIVER TURTLE NESTS
Review round: 3
Reviewer: 2

Output:
Basic reporting: This paper has relevant information about turtle conservation and community-based conservation that deserves publication.

I am mostly satisfied with the responses to the previous concerns raised. However, I still have a major concern regarding detection that I think should be dealt with or at least acknowledged as a potential source of bias. I explain this in more details in the experimental design section.

Ln 323-329: Although subsistence consumption of wildlife is allowed, many people are afraid of enforcement because the law is ambiguous and because of the negative history of local communities with enforcement agencies. Local communities often cite outsiders as the problem, but that does not mean outsiders are the main problem. Without further evidence of "outsiders" being the problem, I don't think the authors can make that claim. It is just a speculation and it should be stated as such.
Ln 379-385: I did not see any data on community values. Do you have these data? You mention meetings. Did you collect data during these meetings? If so, please add. If you are basing this only on your perceptions, please make that clear.
In lines 391-393 you say you are hypothesizing that "respectful and practical engagement along with good will are the most important drivers in explaining the success". Yes, this is a hypothesis. However, in lines 402-405 you say that "that the good will, mutual understanding, and collaborative development of conservation initiatives between local communities, researchers and conservationists are the vital/keystone components for the success of conservation". Do you have any data on the interviews/meetings that you could provide (quantitative or qualitative) to substantiate this claim? You say you performed meetings and interviews with community members, right? If you could add some information about these meetings and these interviews, the claims you are making about why the community-based effort is working would be substantiated. Otherwise, you are just basing these claims on your perceptions of what is happening (and that should be made clear).
Experimental design: Research question and methods are well described.

Regarding detection probability, I understand that the authors used a consistent method and used at least one person throughout the study to decrease bias. However, detection probability does not depend only on the consistency of methods or observer bias, it depends highly on environmental conditions. For instance, the probability of detection can vary greatly from year to year depending on how dry or wet the areas were, on how much vegetation there was, on the level of the river, etc. Given that you cannot possibly detect all nests (which the authors themselves acknowledged previously), they cannot assume detection probability remained the same across the years.

If your data allows you to measure detection probability, then you can eliminate that issue. If not, you need to explain how the potential changes in detection probability (due to environmental conditions, not due to observer bias or changes in methods) may or may not affect the results.
Validity of the findings: If the authors can adequately address the issue of detection, the results can be considered robust and valid.
Additional comments: No additional comments


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

Input:
Title: SEXUALLY DIMORPHIC VENOM PROTEINS IN LONG-JAWED ORB-WEAVING SPIDERS (TETRAGNATHA) COMPRISE NOVEL GENE FAMILIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: The following statement that wandering behaviour reduces dimorphism in feeding biology requires citation or additional evidence, as it is central to the focus of the paper:
“… both males and females wander in search of prey, thus reducing dimorphism in feeding biology”.

2. The reference {Maretic:1964um} (Line 48) is not formatted.
Experimental design: no comment
Validity of the findings: 1. The results do not fully support the hypothesis proposed – that is, that the unique male components in venom play some as yet undescribed role in mating biology. The null hypothesis – that the unique male components in venom do not play any role in mating biology, or perhaps play a role in male-specific predator/prey interactions (as is proposed for the female specific venom components), based on the data presented, cannot be discounted. The GO annotation results, loosely linking the proteins to “hormone function” is tenuous evidence at best and has been overinterpreted to fit the hypothesis.

The inability of the presented data to discount the null hypothesis or alternative hypotheses appears to be acknowledged in some part by the authors. However,  the idea that the unique male components in venom play some as yet undescribed role in mating biology still remains the central theme around which the paper is written. The data clearly showing sexual dimorphism in venom composition, by itself is of considerable interest, and if this were the central theme of the paper (with the idea that the unique male components in venom play some as yet undescribed role in mating biology confined to the discussion and clearly indicated as speculative), I would have, without hesitation, recommended the articles acceptance in PeerJ.

I suggest the article be restructured with these points in mind. i.e. to follow the layout in the current abstract (which is well written and well-structured for the data). In the introduction deemphasise the idea of sexual selection - much of this could be shifted to the discussion and more clearly indicated as speculation.
Much of the Discussion and Conclusions section could simply be removed or reworded e.g. Lines 335, 408, 445 - the words "support" and "supporting" are used. In this context, it more accurate to say "consistent with". At the moment these sections do not clearly show that the points made are essentially speculative.

2. A final related point that I suggest needs to be covered in the Discussion: A high molecular wight protein seems an unlikely candidate as a pheromone… Small volatile compounds can act as pheromones while proteins typically take effect only on injection. Is there any evidence for injection of venom on mating?
Additional comments: While my review may come across as overly negative, I do think the article is exceptionally well written. However I am concerned that the data has been overinterpreted to fit a particular hypothesis. I have suggested a "major revision", but only in terms of restructuring what is already presented in the article.


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: SEXUALLY DIMORPHIC VENOM PROTEINS IN LONG-JAWED ORB-WEAVING SPIDERS (TETRAGNATHA) COMPRISE NOVEL GENE FAMILIES
Review round: 1
Reviewer: 2

Output:
Basic reporting: ok
Experimental design: ok
Validity of the findings: the data are robust, but the conclusions should be improved. Please see my suggestions under general comments for the author.
Additional comments: The manuscript entitled "Sexually dimorphic venom proteins in long-jawed orb-weaving spiders (Tetragnatha) with potential roles in sexual interactions" submitted by Zobel-Thropp et al. is a very interesting study that investigates intraspecific variations in the venom composition based on the gender of the spiders. The authors use transcriptomic and proteomic techniques to identify the differences in venom composition between male and female Tetragnatha species. While the methods that the authors employed are state of the art and the experimental part and data analysis are carried out appropriately, I am not quite convinced by their discussion. In particular, the suggestion that the large molecular weight components that were specific to male venom, would be involved in sexual communication sounds rather unlikely to me. In arthropods, molecules used for chemical communication (incl. sexual pheromones) are usually small and volatile, so they can easily reach the respective recipient. In the present case, I don't quite see how the > 100 kDa male-specific components could be used for chemical communication. I would strongly doubt that such large proteins are volatile. And, while the authors mention the cheliceral locking during mating, according to my understanding that locking does not involve the injection of venom components from one individual to another. Thus, how do the authors think that these proteins are "communicated" or transmitted between the spiders? Or by what other mechanism could they be involved in the chemical communication? I think the authors need to either support their hypothesis more strongly or get rid off it entirely.

What is also quite interesting to me is that this study is not the first one to show some large proteins in the venom of male but not female spiders, as this has already been reported for Phoneutria nigriventer (see Herzig et al., Toxicon 2002). However, in the latter case, there is no cheliceral locking involved in the mating of P. nigriventer. I would therefore strongly question whether the large male-specific components are related to the cheliceral locking mechanism. The interesting question would be what else could they be doing? So the authors should discuss this in more detail.

I also have some minor issues that need to be fixed.

•	L. 60: no bracket in front of Kuhn-Nentwig
•	L.100: "evidence for" instead of "evident"
•	L.134 ff: It would be interesting if the authors could include the venom yields for the different sexes.
•	L.266: the authors should provide the appropriate references for NCBI and ArachnoServer
•	L.435: The statement " we have shown that the venom of Tetragnatha spiders can potentially serve in in both mate recognition as well as adaptive specialization for prey" has to be toned down, since this has not been shown by the authors - it's only a hypothesis (which I am not quite convinced of).
•	L. 455 ff. In the references section, the authors need to make sure that ALL of the genus and species names are in italics. Furthermore, for some of the references, they have all words in the title start with capital letters, but not so for other references. This needs to be consistent for all references.
•	L.590: the current version of WSC is 18.5, so this needs to be updated.


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: SEXUALLY DIMORPHIC VENOM PROTEINS IN LONG-JAWED ORB-WEAVING SPIDERS (TETRAGNATHA) COMPRISE NOVEL GENE FAMILIES
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The revised manuscript entitled "Sexually dimorphic venom proteins in long-jawed orb-weaving spiders (Tetragnatha) comprise novel gene families " submitted by Zobel-Thropp et al. has now been substantially improved in comparison with the previous version.

Except for some minor points (see below), I think the manuscript is almost ready for publication.

•	L75-76: Another explanation for the "higher mammalian neurotoxic" activity could just be that males are a lot smaller and therefore yield substantially smaller venom amounts. I don't think that the chosen reference (Maretić, Levi & Levi, 1964) provides sufficient evidence for either case, as they don't really compare similar amounts of venoms from both sexes. Hence, other references need to be included to support this statement or it has to be removed.
•	L92: "that are not (found/present ?) in females"
•	L.360ff: "The high molecular weight components in male T. versicolor venom may be characteristic of the genus Tetragnatha" - based on similar observations from P. nigriventer venom, that statement is not true. Or did the authors mean "characteristic for male T. versicolor within the genus Tetragnatha"?
•	L430: should that read "toxins" instead of "venoms"?
•	Re. my previous comment on the venom yields: in case the authors have recorded the average male and female venom yields (rather than the individual yields), such data would also be interesting to report.
•	Re. the terminology of peptides/proteins, I think the common rule is that anything above 10 kDa is termed protein, whereas anything below is termed a peptide. Hence, the high-molecular weight male venom compounds should be termed as proteins (rather than polypeptides).
•	L519: should the "11" be in front of "Edited" or is this a typo?
•	L486: some references still have all words starting with capital letters in the title, which should be changed.


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: SOME LIKE IT HOT: FACTORS IMPACTING THERMAL PREFERENCES OF TWO PONTO-CASPIAN AMPHIPODS DIKEROGAMMARUS VILLOSUS (SOVINSKY, 1894) AND DIKEROGAMMARUS HAEMOBAPHES (EICHWALD, 1841)
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper of Rachalewski is mostly written in a clear and unambiguous English. Slight linguistic changes might be necessary. The introduction shows the background and context of the study well, although I do not concur with all statements (see general comments). The literature is well referenced and relevant. The structure of the paper conforms largely to PeerJ standards although some information are missing (see general comments). All figures are relevant and of good quality. I would like more information in the figure description (such as number of experimental repetitions, number of infected/uninfected animals). The raw data are partly supplied. I’m not exactly sure how to read the data file. Is the ID in the column “Aquaria” the ID for the specific experiment? I feel that the values for temperatures in the single partitions of the flume are lacking.
Experimental design: The research presented here is original primary research well within the scope of the journal. The research questions (in that case 3 hypotheses) are well defined and meaningful. The questions are relevant and it is clearly stated in the introduction how they will fill a knowledge gap. However, I do not see, how the hypothesis 3 and 4 tested with the data set presented here. It is only possible to describe the temperature preferences and possibly their changes due to parasites. It will however not be possible to discriminate between behavioural fever and parasite induced behavioural changes because the observed shift in the thermal preferences would be the same and no mechanistic analysis has been performed.
The experimental design, using temperature gradients in flumes during multiple trials is sound and the number of replication (n=20) seems adequate. The fact that the experiments contain individuals of different sex and infection status might represent an experimental problem because the individuals of the different groups might interact with one another. However, I do not see how this problem might have been avoided, because the sex-determination of living animals represents quite a lot stress for the animals and I belief a sound determination of infection status is not possible at all. However, the problem should probably be addressed in the discussion.
The description of the methods is not sufficient to evaluate the data and to replicate the experiments in its present form. I belief following information are missing: time of sampling, accuracy of species determination on living animals, reproduction status of females (carrying eggs?), temperature of experimental compartments (and its variation), kind of water used for keeping and in the experiments, chemical and physical conditions during the experiments (oxygen, conductivity, ammonia concentration), how was the sampling accomplished in the flume without allowing the animals to change their position. I expect that each individual was only used once. However there is no mention of that fact in the methods. In addition, there is no information regarding the statistical software used.
Validity of the findings: Although the experiment might conducted correctly, which I cannot assess because of the missing information, I feel that the statistical analysis is not adequate. The authors use the temperature at which every single animal was observed after 30 min as the response variable. The aim of the statistical test is however to find a potential shift of the temperature preferendum. Consequently, the temperature preferendum should be used as the response variable. In addition, the method used by the authors handles every single individual as an independent n, which is not true and uses the respective trial as random factor. In my opinion, the trials are real and independent replicates and the animals within each trial pseudo-replicates. And as the temperature preferendum is addressed in this paper, I recommend that the authors use the median or mean temperature of each trial as response variable (see for instance Reiser et al 2014, http://dx.doi.org/10.1016/j.jembe.2014.08.018; or Haupt et al in press http://dx.doi.org/10.1016/j.jinsphys.2016.12.006 ). In addition, such behavioural experiments often produce artefacts because individuals become caught at the temperature extreme due to physiological stress and consequent loss of mobility. Because the distribution in case of D. villosus is skewed towards the upper end of the temperature gradient, this aspect should be at least be addressed in the discussion.
I cannot assess, whether the conclusions are supported by the data provided here due to the above mentioned statistical issues. This would have to be assessed after a revision of the manuscript.
Additional comments: As mentioned above, the paper is well written, focussed on a clearly specified and relevant research question and therefore well within the scope of PeerJ. However, I feel that there are a lot of information missing to evaluate the method of the study and the validity of the data. In addition, I see major problems with the statistical analysis used here (see Validity of findings). Especially the right-skewed distribution of the relative abundance might be an experimental artefact unless there is in fact an 11th compartment that was hardly used by the animals (>38°C). However, as only 10 compartments are mentioned, I wonder why there are 11 temperature classes in the figures.
Further, I see some problems in the introduction. The authors state, that amphipods are a good model to study temperature preferences (L89 and 106) but do not support the statement sufficiently. It is not clear to me, why amphipods in general and Ponto-Caspian amphipods specifically are such a good model. In addition within the introduction, Rachalewski et al point out that temperature preference is an important species trait regarding invasional success (L108 f). However, firstly they do not support their statement with valid citations (containing real data and not only general assumptions) and secondly it is not really the point of the paper.
I do not comment the discussion here because I assume that after reanalysing the data, some statements might have to be changed. Generally, the discussion seems not to be completely focussed on the research question and might contain some slight over-interpretation of the patterns observed here, especially in the light of potential experimental artefacts.


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: SOME LIKE IT HOT: FACTORS IMPACTING THERMAL PREFERENCES OF TWO PONTO-CASPIAN AMPHIPODS DIKEROGAMMARUS VILLOSUS (SOVINSKY, 1894) AND DIKEROGAMMARUS HAEMOBAPHES (EICHWALD, 1841)
Review round: 1
Reviewer: 2

Output:
Basic reporting: Specific comments:

L 36: To avoid confusion about the species of the males, I suggest reversing the order of this phrase “females of D. haemobaphes and conspecific males” to “conspecific males and females of D. haemobaphes”.

L 64, 90: Omit “the”.

L 67: Insert “the” before “preferred”.

L 106: Change “upon” to “about”.

L 107: Change “resistance” to “tolerance”.

L 109: Change “What is more” to “Furthermore”?  Insert “their” before “native”.

L 126-146: I am a bit puzzled by the placement of parenthetical numbers in this paragraph.

L 158: Change “to the temperature of 20°C” to at “at 20°C”.

L 179: Change “to” to “and placed in”.

L 180-181: Somewhat awkward wording.  Change “to identify their sex and proceed the molecular screening for the microsporidium presence and identification” to “for sex identification and molecular screening of microsporidia”?

L 217-219: Run-on sentence.  Replace comma with semicolon between “microsporidea” and “however”.

L 220: Replace “while” with “whereas”.  The word “while” has an unintended temporal connotation.  Insert “was infected” before “by”.

L 249: Please clarify what is meant by “a similar effect”.  What kind of similar effect?

L 256: Change “What is more” to “Furthermore”?

L 257: Change “large, receptive females are assessed by males as more attractive” to “large, receptive females are more attractive to males”.

L 258-260: Better references would be:

Wijnhoven et al. (2003). Exotic and indigenous freshwater gammarid species: physiological tolerance to water temperature in relation to ionic content of the water. Aquatic Ecology 37, 151-158.

Maazouzi et al. (2011). Ecophysiological responses to temperature of the “killer shrimp” Dikerogammarus villosus: is the invader really stronger than the native Gammarus pulex?. Comparative Biochemistry and Physiology Part A: Molecular & Integrative Physiology 159, 268-274.

These studies actually show how respiratory pleopod beating increases with increasing temperature in one of the species studied by the authors.

L 272: The word “proved” seems too strong.  Are you 100% certain?

L 276: Which authors?

L 285: Change “though” to “although”?

L 293: Change “upon” to “on”.

L 300: Change “we were” to “were we”.

L 302: Change “at the higher temperature” to “at higher temperatures”.

L 310: Change “by trophic way” to “trophically”?

L 320: Change “in consequence” to “consequently”.

L 336: Change “to a range of 0 – 40oC” to “as ranging from 0 – 40oC”

L 344-345: Make more concise.  Change “only in very few studies upon invertebrates of different taxonomic classification” to “in few invertebrates”.

L 358: Insert “by” between “for” and “their”.

L 364: Change “reproduction” to “reproductive”.

L 369-371: If D. villosus is more effective at preventing or eliminating infection by microsporidia, then why does this species show higher percent infection than does D. haemobaphes (as shown in Table 1).

L 374: “we may assume”?  Did they show more complex thermal behavior or not?  Isn’t this an observation, rather than an assumption?

L 378: Omit “applied”?

L 379: What is “it” referring to in this sentence?

L 381: Change “among” to “between”.  Change “while” to “when”?

L 383, 387: Omit “the”.

L 386, 392: Change “The knowledge upon” to “Knowledge about”.

L 386-387: Change “the community” to “communities”.

L 393: Insert “an” before “extremely”.

Figures 2 & 3: What are the error bars?
Experimental design: Good.
Validity of the findings: Good.
Additional comments: This paper presents useful data on how sex and microsporidian infection affect the thermal preferences of two species of invasive amphipods.  Overall, the paper is well organized and presented.  The data analysis also seems sound.  I have only relatively minor comments, given above under Basic Reporting.


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: ASSESSMENT OF THE ECOTOXICITY OF URBAN ESTUARINE SEDIMENT USING BENTHIC AND PELAGIC COPEPOD BIOASSAYS
Review round: 1
Reviewer: 1

Output:
Basic reporting: This study brings a contribution for aquatic ecotoxicology using copepod bioassays in estuarine sediment biomonitoring.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: The term "in situ" is not applicable to this study, because the tests were carried out in laboratory. Please verify the use of this term in the text (e.g., L 59-60) and in the abstract (L. 30).
Methodology:
- How long the samples were stored until the tests were carried out? (L. 88).
- Please provide details about elutriate preparation (L. 94).
- Please provide the author of the species cited in this study.
- What is the source of "mixed algae"? Which species? (L.112)
- Please cite the protocol that was followed to cultivate the aquatic organisms in lab (L. 103-113).
- Please provide more details about the sediment tests to allow the reproductibility of this study by other researches (L 114-121).
- Please standardize the terms. E.g., "waterbourne toxicity tests" (L. 123) should be replaced by "elutriates toxicity tests".
- These references are not provided in the reference section: HBCR 2014 (L. 50), ASTM 2000 (L. 125), USEPA & USACE 1998 (L. 125), ISO 16778 (L. 133), ISO 2016 (L. 199).
- What the term "development rations" means? (L. 142).
- Please provide a reference to the statistical analysis (L. 171-178).
- Tables 1 and 2 are exchanged in the text (L. 182 and 186).
- L. 115, please complete “Chandler & Green” (1996).
- L. 196, "arsenic" or "cadmium"?
- L. 252-254. Please clarify. Why lower concentrations of metals induced higher DNA breaks than higher concentrations?
- What is the reason for effects on survival but not in development?


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: ASSESSMENT OF THE ECOTOXICITY OF URBAN ESTUARINE SEDIMENT USING BENTHIC AND PELAGIC COPEPOD BIOASSAYS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The study presented in the manuscript can be considered in correct English. However, line 21, the species name is misspelled; line 38, should be lives; line 123 is waterborne.

The Literature references are adequate (n = 70), however there are many studies with more than 5 years (<2013, n = 47) and few current studies (≥ 2013, n = 23).

I believe that “water column toxicity” is not the correct term, due to the fact that you are working with elutriate (line 194).
Experimental design: In the material and methods section, line 111 to 113 (test species), you should improve the description of the protocol for cultivation of these species in the laboratory (e.g.: photoperiod; room's conditions or hatchery equipment used; mixed algae: which species,...). Some of them, you describe later in the toxicity test section, but are missing in the test species section.
Validity of the findings: Please check, I believe the order of tables 1 and 2 have been changed, as well as table S1.

Lines 199 to 202, you started describing the results of Fig 3B and after Fig. 3A. I believe you should change the order of the graphs in the figure or in the text, to be clearer for the reader.

Line 202, please add the letter "B" when you mentioned "Fig. 3" (Fig. 3B).

Line 210, you mentioned that a significant difference was identified at some endpoints of DNA damage. I think the tail length graph is missing.

Also in line 210, you mentioned that "there were no difference between the tail moment from the negative control and the estuary sites" (Fig. 4). I believe you should also include the tail intensity.

However in line 212, please check, but I believe you could not affirm that the Humber Drain samples induced DNA damage as indicated by the tail intensity.

In table 3, "*" is missing in the concentration of Zinc of Humber Drain (75 μg/L).

In the discussion section, you mentioned high and low concentration and effects of other studies to discuss your results. However, you should include the results of those studies to determine or to be clearer what you consider as high or low values.
Additional comments: The study presented in the manuscript can be considered relevant. Although, the references used in the introduction and discussion may be more current.

The study also indicated that further studies are needed to conclude which chemical compounds were most influential in the toxic effects on the copepods of the estuarine sediment. Since the chemical compounds analyzed did not fully answer this question. Due to the fact that the reference area presented some metals and the toxicity was detected in some bioassays, this should have been better discussed 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: URBANIZATION ALTERS SMALL RODENT COMMUNITY COMPOSITION BUT NOT ABUNDANCE
Review round: 1
Reviewer: 1

Output:
Basic reporting: In general, the manuscript is well-written. However, there is some imprecise and inaccurate use of terminology. For example, throughout the manuscript, instead of referring to the study organisms as ‘small mammals’ or ‘rodents,’ the authors often refer to ‘herbivores’ and ‘small vertebrates’ – both of these terms encompass many species other than those studied here. But, more importantly, many of the small mammals in this study are not actually herbivores, but rather granivores (for example, Dipodomys spp.) or omnivores (Peromyscus spp.).

Figure 1 needs a scale bar. Currently, it is impossible to tell how far apart the sites are.

In the Figure 2 caption, n should equal 4, not 8, because there are 4 sites/treatment.

There are several places in the manuscript where the writing should be tightened or clarified:

Lines 22-23: This sentence is unclear – “led to equally reduced plant biomass” – as compared to what?

Line 61: The use of “distribution” here is awkward. I’m not sure that the distribution (do you mean range?) of a species is necessarily reduced by anthropogenic effects, although the distribution could certainly change as a result of human influence.

Lines 62-63: This is an incomplete sentence.

Line 67: Again, what does “equally reduced biomass” mean?

Line 72: The reference to “vertebrates and plants” strikes me as odd. It leaves out invertebrates entirely, and then the sentence goes on to refer to “the plants they eat.” This is really unclear, because as written, the sentence implies that plants eat plants.

Line 151: It is unclear what is meant by “abundance” here – are the authors referring to abundance by individual species, or to total small mammal abundance including multiple species?
Experimental design: The authors investigate an important and timely question: how urbanization affects populations of native animals. Unfortunately, the experimental design is flawed, and the sampling strategy does not actually yield the data needed to test their hypothesis. The critical issue, and one that can’t be fixed at this point, is that traps were not distributed across the study areas in an unbiased way (lines 121-122). To be able to make a valid comparison of small mammal presence and abundance across sites, traps should either have been randomly distributed (for example, by generating random X,Y points and placing traps at those points), or in a consistent pattern such as a trap grid, web, or line. By “scattering” traps and placing them in locations where animals were more likely to be captured, the authors biased their data. This approach is fine if the only objective is to capture as many animals as possible (perhaps for behavioral studies of a particular species, for example), but completely inappropriate if the goal is to determine the species and numbers of animals present in an unbiased way. By selectively placing traps in certain types of microhabitats, the authors have potentially overestimated the abundance of certain species and missed others entirely.

There are also concerns with the statistical analysis. The authors did test for normality of the data, but with such small sample sizes (n of 4 in each category), such a test is of limited utility. I would suggest the use of non-parametric tests instead. I am also concerned with the NMDS, because of the way in which “unknown” animals and individuals that were classified to genus but not species were included. Inspection of Fig. 3 reveals that these categories of animals are de facto treated as separate species. This means that there are 5 “species” included in this analysis that are not real:UK, ChSpp, PmSpp, NeSpp, and OnSpp. In effect, this takes individuals from multiple actual species within the genus and lumps them together, which is problematic in multiple ways.

The authors did have the appropriate permits and protocols, but need to include the university that approved the IACUC protocol (I assume ASU, but this is not stated).

There are much more recent guidelines for the care and use of mammals in research from the American Society of Mammalogists – I believe the most recent set was published in 2016, and is freely available on the ASM website.
Validity of the findings: Unfortunately, the data were collected in such a way that they cannot actually be used to test the hypothesis posed in this manuscript. The authors could reanalyze their data in more appropriate ways (such as removing the animals that were not identified to species from the NMDS), but because of the bias in the trapping strategy and therefore the underlying data, valid comparisons between urban and outlying areas cannot be made.
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: URBANIZATION ALTERS SMALL RODENT COMMUNITY COMPOSITION BUT NOT ABUNDANCE
Review round: 1
Reviewer: 2

Output:
Basic reporting: Very good, no problems
Experimental design: Very good, no problems
Validity of the findings: Very good, no problems
Additional comments: A very nice contribution to the literature, well written and well implemented. My only suggestion is that you cite and add a discussion of the article below, which is a meta-analysis of papers documenting abundance changes in urban habitats. Your paper should be placed in the context of their results: does it fit? If not, then why? Also, they discuss mechanisms of abundance change: how do your results compare to their suggested mechanisms?

Urbanization is not associated with increased abundance or decreased richness of terrestrial animals - dissecting the literature through meta-analysis
By:Saari, S (Saari, Susanna)[ 1 ] ; Richter, S (Richter, Scott)[ 2 ] ; Higgins, M (Higgins, Michael)[ 2 ] ; Oberhofer, M (Oberhofer, Martina)[ 3 ] ; Jennings, A (Jennings, Andrew)[ 3 ] ; Faeth, SH (Faeth, Stanley H.)[ 3 ]
URBAN ECOSYSTEMS  Volume: 19  Issue: 3 Pages: 1251-1264 DOI: 10.1007/s11252-016-0549-x
Published: SEP 2016  Abstract
The widely accepted consensus is that urbanization increases abundance but reduces species richness of animals. This assumption is the premise for empirical tests and theoretical explanations. We studied the association of urbanization with abundance and species richness of different animal taxa in 20 and 26 published articles reporting abundances and richness, respectively via meta-analysis. Because some articles had multiple estimates, we analyzed 40 and 58 estimates of abundance and richness, respectively. Contrary to conventional wisdom, the overall abundance of terrestrial animals was not higher in urban areas, but instead actually lower, while we failed to confirm the conventional thinking of lower species richness with urbanization. These findings cannot, however, be generalized across all cities and animal species, as conflicting differences were reported among geographical regions, animal taxa. Our results question the conventional wisdom that urbanization generally increases abundances while reducing species richness, and highlights the variability of urbanization effects on diversity among taxa and geographic regions.


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: MULTI-DIMENSIONAL PRECISION LIVESTOCK FARMING: A POTENTIAL TOOLBOX FOR SUSTAINABLE RANGELAND MANAGEMENT
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article is clearly written, and it is an important topic to study. The introduction and methods are clearly presented, although more details in the introduction would be beneficial (see later comments). The results section is a bit more difficult to follow, and there are some mistakes in the labelling of some of the figures. The discussion is however more of a series of the potential applications of the findings, whilst discussion on the method used would have been also interesting.
The raw data have been supplied, and, in places, maybe could have been included in the manuscript as figures.
Experimental design: The experimental design is clearly explained, although in places, more details would be useful. As it stand, it is difficult to really understand how many animals in total were involved, how long they got the sensors on, how many observers during the training set period, how long after the initial training session were the data recorded for.  Also, there is no clear presentation on how the comparison and correlations were made – which stats package, which tests? It would be helpful to know this information .
You also need to explain why 3 sheep are enough for the experiment.
Validity of the findings: The results do not appear to present everything – I would have liked to see some information on the training dataset results. Also, a lot is inferred on only 3 sheep – so is it a case of lots of data for not many sheep, which is a trade off? This should be shown better.
It is not clear if the approximation of costs is purely based on energy costs, this should be explained.
In the discussion, I think that a paragraph detailing why 3 sheep are enough to infer the results is necessary. Did other studies have so few animals? Also, what about seasonal variation, animal variation, would it have been useful to rotate the 3 collars among different individual to obtain more data? This should be discussed. I also feel that lines 306-319 should be in the introduction, not the discussion.  I also think that the section on management & ecological applications should be called ‘potential management & ecological applications’.  In that section, the affirmations should be more cautious, using ‘could’ instead of ‘can’.
I am not sure if it is appropriate to include references in the conclusions.
Additional comments: More detailed comments below:
Title: I suggest you say: Multi-dimensional PLF – potential toolbox for sustainable rangeland management.
Introduction. I would add the section in the discussion (306-319) in the introduction
Line 48 – more definition of PLF would be good
Line 61 – more reference to this fact would be good
Line 71 – reference on PLF with wild species (e.g. GPS on deer, etc.). I would also add some reference to wild species monitoring.
Perhaps add a section on conflicts between the livestock and wild species would be useful.
Line 94 – Merino sheep – why sheep? Perhaps explain that there are few studies with sheep – most of PLF at present is on cattle or dairy or monogastrics.
M&M:
Line 108 – what do you mean by 1) low productivity zones?
Line 115 – how was the predation risk defined? Please explain a bit.
Line 118 – how many sheep in the paddock in total? Only 3 sheep on 90 ha? If you had more sheep, how did you choose them? What age were they? Were they naïve to the land? Were they related to each other, or did they come from the same original flock? All of these are important because of the gregarious nature of sheep.
Line 129 – how long did you measure the data after the initial training? This is not explained.
Line 131 – how many observers during the training data period?
Line 144-145 – I would reference Umstatter et al. 2008, who used similar approach.
Line 178 – competition level – how did you assess these?
Line 217 – how do you obtain intake rate from bite rate? Formulas exist in the literature (e.g. see Illius & Gordon in the late 90s who worked on these issues)
Results:
Line 239 – high classification accuracy – what is from the training set? You should precise this.
Line 261 – searching time vs less heterogenous distribution of resources – perhaps you should reference this.
Lines 268-269-271 – Figures 4, 4a, 4b – these are not in the figures list – it looks like there has been a switch between the figures, they do not correspond to the text.
Line 273 – ‘some animals’ how many? You only had 3 sheep.
Line 277 – predators – what sort of predators do you have in Patagonia? It would be nice to give some examples for the international audience.
Line 295 – ‘some individuals’ – again, which ones out of the 3?
Discussion
Line 330 – I would also cite Umstatter et al (2008) who looked at different behaviours and activities with sheep (resting, ruminating, moving, grazing).
Line 368 – I would say ‘could be that it allows…’
Line 392 – I would say ‘could’ instead of ‘can’


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: MULTI-DIMENSIONAL PRECISION LIVESTOCK FARMING: A POTENTIAL TOOLBOX FOR SUSTAINABLE RANGELAND MANAGEMENT
Review round: 1
Reviewer: 2

Output:
Basic reporting: Language is overall clear and professional and complex ideas are explained with clarity and detail.

Abstract discussion. The first line talking about how the method could determine “variability between individuals” is more methodological than discussion. It should either be related to the discussion more explicitly, moved to the methods / results or removed.

Figure 1a. Could be improved by explicitly linking the tools to the variables and applications. As it is, it doesn’t add much more than is already in the text.

Background, it would be nice to have a short description of how PLF is defined.

Welfare issues – for me it is not clear why the method would improve animal welfare explained why this relates to welfare? Presumably by helping reduce predation or detect lameness etc? It would be nice to have this clarified in the discussion.
Experimental design: The experimental design is robust and detailed. The authors have developed a methodology that extracts an impressive range of variables on animal behaviour and landscape features from the data.
Validity of the findings: The findings are valuable for identifying different animal behaviours that may help improve management and the SMS system would appear to offer great promise for monitoring and managing grazing herds in extensive systems.

Discussion and conclusions are well related to the methods.
Additional comments: The analysis is well presented, and highly relevant for managers seeking to improve productivity while managing grasslands and wildlife conflicts more effectively.

A few minor comments line by line are as follows:

Line 47: Awkward wording. Suggest rephrasing “quantification of detriments….”
Line 55: Suggest inserting word - document “animal” behaviour
Line 66: Suggest being more explicit about the ability of the method to reduce human wildlife conflict with both predators and wild herbivores
Line 96: What GIS system? Describe the source.
Line 139: Agnostic interactions. Please explain what this means
Line 277: “from on” both words are not needed
Line 307: “the” should be corrected to “there”
Line 348: Missing word – ecologically (?) management
Supplementary material S1, Line 24: Pow should be paw


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: MULTI-DIMENSIONAL PRECISION LIVESTOCK FARMING: A POTENTIAL TOOLBOX FOR SUSTAINABLE RANGELAND MANAGEMENT
Review round: 2
Reviewer: 1

Output:
Basic reporting: This revised manuscript now reads very well, and is a very valuable piece of research. I would only suggest adding a precision in the title of Figure 2: "A 15 min [...] with four behaviour (G=Grazing, V=vigilance, S=search, W=walk) performed by a sheep through time".
Experimental design: The added details in the methods clarify it perfectly.
Validity of the findings: The revision in the discussion and results are well done. The changes in the conclusions are also fine.
Additional comments: I have few very minor comments:
-line 66: It is Morgan-Davies (not Morgan-davies)
-lines 108-112 - I am not sure these lines are necessary.
-line 131 - I would delete 'For' and rewrite the sentence as: More details [...] description are in Figs. [...].
-line 155 - I would add: The 6 main behaviours
Line 157 - change 'inside' to 'within'
Line 198 - I would put VeDBA in full letters at this stage.
Line 358 - I would change: ...sometimes difficult to be defined
Line 361 - I would change 'will' by 'would'
Line 384 - I would suggest "For a more theoretical and ecological point of view, we would also encourage future research to apply this technique..."
Line 479 - applied at a global scale.


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: MULTI-DIMENSIONAL PRECISION LIVESTOCK FARMING: A POTENTIAL TOOLBOX FOR SUSTAINABLE RANGELAND MANAGEMENT
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comments
Experimental design: No comments
Validity of the findings: No comments
Additional comments: The updated manuscript is much improved, and I have no further substantive comments.
The manuscript was in good shape originally, but the new edits provide valuable context to strengthen the methodological approach and conclusions.
I have a few minor comments, that are suggestions. I am happy to leave it up to the authors to decide whether they wish to incorporate them.
It is good to go from my perspective. Thank you for an enjoyable review!

*Minor comments*
Line17 / Line 528: The statement that 91% of the world’s surface devoted to livestock production is extensive grazing land is fascinating but has no reference. I appreciate that the abstract likely does not allow references, but I for one would be very interested to know where this figure comes from. Adding the reference to line 528 would be useful I think for many readers.
Figure 1: This is improved and helps create the associations between the methods and factors and activites being observed and managed. I didn’t see any reference to section 1A in the text though? Line 51 refers to Figure 1, and lines 92 and 94 to Figure 1B. This is an extremely minor point, but having taken the time to produce 1A, it may be worth referring to it where you discuss the tools used to document behaviours (lines 52 – 54).
Line 54: The phrase “PLF consists in….” would read better if it were changed to “PLF utilizes….” or similar
Line 439: “a” is unnecessary
Line 524: Please be (briefly) explicit about why more environmentally and wildlife friendly livestock management practices have economic benefits – is it because they can charge more for their products to environmentally conscious consumers? Or because the obtain some value from wildlife such as through tourism? Or some other process?


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

Input:
Title: CHARACTERIZATION OF TUMOR HETEROGENEITY BY LATENT HAPLOTYPES: A SEQUENTIAL MONTE CARLO APPROACH
Review round: 1
Reviewer: 1

Output:
Basic reporting: The English could be improved - some sentences are difficult to follow.

Some examples include:

In the abstract, the authors say “..and the parameters of our proposed state-state model.”  I assume they mean “state-space model.”

Lines 52-54:  Use of both “Although” and “however” makes this sentence confusing.
Line 82:  authors should define “IBP” (Indian Buffet Process) in the main text.
Line 93:  authors introduce matrices Z and W with no context or definition
Line 112:  “SOME LATEX EXAMPLES”; I’m not sure why this is here.

Also, citation of Wersto et al. does not make sense (Line 41).  The context involves studies that investigated tumor heterogeneity using NGS technology – Wersto et al. looked at tumor DNA content using flow cytometry.  Additionally, the necessary depth of sequencing necessary to characterize somatic variation is quite high, making it rather dubious to claim such studies have been conducted for the “past few decades”.
Experimental design: There are other similar approaches that were not addressed.  The most obvious comparator would be the MAD-Bayes approach proposed by Xu et al. (JASA 2015), which similarly touts computational benefits over MCMC-based inference and applies IBP priors for feature allocation.  It would seem important to compare against this approach.  However, it is not mentioned in the manuscript and its unclear why the authors did not investigate.
Validity of the findings: The methods appear well-outlined and the modes of evaluating error in the simulations seem reasonable.
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: CHARACTERIZATION OF TUMOR HETEROGENEITY BY LATENT HAPLOTYPES: A SEQUENTIAL MONTE CARLO APPROACH
Review round: 1
Reviewer: 2

Output:
Basic reporting: Some typos must be fixed. Some sentences are too long.
Experimental design: Will the code to reproduce your results be publically available? How can other research teams apply your algorithm?
Validity of the findings: The findings on the synthetic data show some improvement over MCMC, but there are many alternative approaches to compare with. Also, no validation on the real data.
Additional comments: === Summary:
  The manuscript describes an approach to estimate the clonal structure of a tumor using multiple samples obtained from a single cancer that vary patient spatially or temporally. This work may be have some methodological contribution to the field. In particular, the authors claim to use the spatial and temporal information on the samples in their inference. However, while they used the Chinese Restaurant Process to the include the temporal information in the analysis, it is not clear where and how the spatial information is used in their model. Also, comparison with the current approaches is very limited.

=== Major:
- How can your approach be used on multiple samples that vary only spatially? Do you assume that all samples are "sequential" in the sense the they are taken along a line? Discuss if and how can your approach be extended in 2 or 3 dimensions. Also, what if both time and space vary together?

- In the real dataset, how do you compare your results vs. MCMC? Did you use any gold-standard to determine which approach was actually better on the real dataset?

- There are several other approaches that have been developed to do a similar task including: Clomial, cloneHD, PhyloWGS, PyClone, Cloe, phyC, Canopy, TargetClone, ddClone, PASTRI, GLClone, TRaIT, WSCUnmix, and B-SCITE.  A fair comparison with some of these alternative approaches is desirable.

=== Minor:

- The abstract is somewhat too technical. Please consider rewriting it for a broader range of audience especially biologists who are not necessarily interested much in the technical and methodological details. For example, explain why and how your sequential algorithm could be better.

- Some sentences are too long, e.g., lines 30-34, 40-44, etc.

-"These approaches have several limitations that prevent their wider usage in examining and quantifying the level of heterogeneity in a given sample." Briefly, mention these limitations.

- Typo: "112 SOME LATEX EXAMPLES"

- When referring the literature, please consider citing the original work. For example, a version of Eq. (2) has been mentioned and used in (Zare et al. 2014) before (Lee et al., 2016).

- Typo: "(Griffiths and Ghahramani, 2011; ?)"

- Typo: "then such a binary matrix is a draw from the distribution in (3) (?)"

- Line 154: Remove "due to limited space".

- Line 136: Remove "(discussed below)".

- Typo: 194 Reference to Figure ??.

- Typo in the supposed: "The CLL datasets in [3] for the three patients and the prostate cancer dataset are presented in Tables 21 - ??." Also, did you analyze and explain a prostate cancer dataset?!

- In the caption of Tables S1-3, explain how they are different from the tables in the main 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: CHARACTERIZATION OF TUMOR HETEROGENEITY BY LATENT HAPLOTYPES: A SEQUENTIAL MONTE CARLO APPROACH
Review round: 1
Reviewer: 3

Output:
Basic reporting: In general, there are numerous grammar error and typo throughout the manuscript. For example, the sentence on page 9 line 230 has a grammar error.

Page 4 before equation (3), “Griffiths and Ghahramani, 2011; ?)” and Page 4 line 150 (?). There are many unexpected question marks all over the manuscript. Please correct them.

Page 3, line 112 and page 7, line 194 should be deleted.

The English language should be improved and partially rewritten.
Experimental design: Please add some instructions and examples to run the source code. I did not find any instruction on the github: https://github.com/moyanre/tumor_haplotypes
Validity of the findings: The authors claimed that the proposed SMC algorithm benefits from larger number of loci. But the haplotype error (ez) in table 2 increased from 0 to 0.008 of 1000 loci and 2000 loci respectively, which is exactly opposite to this conclusion. It would be better to make an explanation for this phenomenon.

In CLL003 data analysis part, the proposed SMC algorithm identifies 7 latent haplotypes, C2 and C6 are dominate haplotypes which is not consistent with Manual and Phylosub method, since Manual and Phylosub yield 5 haplotypes and only one of the haplotype dominate others(with ~0.8 proportion). How to interpret the difference? The inconsistency of estimated haplotype happened in CLL006 and CLL077 as well. The CLL data analysis part should be improved.

It will be great if the authors can compare the SMC method with some well known subclonal reconstruction methods such as PyClone.
Additional comments: This paper presents a novel sequential Monte Carlo (SMC) algorithm to solve the feature allocation model which characterizes tumor heterogeneity by latent haplotypes. Based on the simulated data, the proposed SMC algorithm provides more accurate compared to the state-of-the-art Markov chain Monte Carlo (MCMC) approach. An additional feature of the proposed algorithm is that newly observed VAFs data from next-generation sequencing (NGS) can be analyzed to improve existing estimates without re-analyzing the previous datasets, which improve the efficiency.
The effort to develop a more accurate and efficient algorithm to infer latent haplotypes is valuable.


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: CHARACTERIZATION OF TUMOR HETEROGENEITY BY LATENT HAPLOTYPES: A SEQUENTIAL MONTE CARLO APPROACH
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors have addressed my concerns.
Experimental design: The authors have included competing approaches with similar formulations and subsequently strengthen their manuscript.
Validity of the findings: No concerns.
Additional comments: The edits and alterations have improved the manuscript and I  have no further comment.


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

Input:
Title: CHARACTERIZATION OF TUMOR HETEROGENEITY BY LATENT HAPLOTYPES: A SEQUENTIAL MONTE CARLO APPROACH
Review round: 2
Reviewer: 2

Output:
Basic reporting: The presentation improved.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: 1- "we included, in the Supplementary Material, the results for PyClone"

I could not find PyClone results in the supp file that I attached. Am I looking at the right version?

2- The authors explained why they called their approach "sequential" in their reply. Did they include this explanation in the revised 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: CHARACTERIZATION OF TUMOR HETEROGENEITY BY LATENT HAPLOTYPES: A SEQUENTIAL MONTE CARLO APPROACH
Review round: 2
Reviewer: 3

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The authors have addressed all of my comments and concerns in the revised version. I have no additional comments. Overall, the proposed method will benefit other researchers in the fields. I recommend to accept the paper.


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

Input:
Title: VARIATIONS IN EARLY LIFE HISTORY TRAITS OF JAPANESE ANCHOVY ENGRAULIS JAPONICUS IN THE YANGTZE RIVER ESTUARY
Review round: 1
Reviewer: 1

Output:
Basic reporting: There are some minor issues with presentation of the text (i.e. spaces between words are occasionally omitted throughout) but the use of English language is quite good.

The use of references from the literature could use some improvement, as there are huge amounts of literature available on anchovy and other similar fish from many regions regarding their growth and analysis of otoliths, but only a small amount of this literature is assessed in this manuscript. Also, some of the references do not seem to be on the topics of the sentences that are placed with e.g. line 36-37. And some large statements are made without providing references, which should be included e.g. line 43.

The figures are good quality, but some of them are not very relevant and are likely not needed. For example, Figure 1 shows a large number of sampling stations, but it appears only 2 of these stations were actually used here, so most of the information is unnecessary. Figure 2 only serves the purpose of showing a photograph of an otolith, which does not provide much information to the reader. Figure 5 and 6 show that as anchovy get older in age, they also get bigger in length and their otoliths get bigger, which is only very basic information which probably does not need to be presented.
Experimental design: The research aims to fill a knowledge gap concerning unknown aspects of early life history of anchovy in the Yangtze estuary, but the design of the experiment is small in scale and in its current form cannot come close to achieving this aim. It appears only two closely spaced stations were assessed here with samples taken during 10 minutes of sampling at each station. Readers will wonder why anchovy samples were not also collected and analysed from the other 32 stations. For example, an analysis of effects from a possible salinity gradient from the stations within the river to the many off-shore stations may make the study more comprehensive and of greater interest. The authors should consider possibilities like this for any re-writing of the manuscript.

From the abstract and introduction it seems to the reader that some new data will be presented also about anchovy in Taiwan and Japan, but when the reader gets to the methods it is clear these data are previously published descriptions from many years previous that the Yangtze data are very informally compared to. Thus the aim stated of inter-population comparisons is also not achieved.

The quantification of otolith properties from the two stations and calculation of population data appears to be done to a high technical standard, but the statistical analysis needs improvement, e.g. the assumptions (data normality and variance homogeneity) need to be tested and more details of the procedures need to be provided, such as the statistical programmes used for analyses.
Validity of the findings: As stated above, more comprehensive data will need to be added to this study before it can be valid for providing relevant information on anchovy in this region. If the authors wish for some valid comparisons with other regions such as Taiwan and Japan, actual new data from those regions will be to be analysed alongside the data from the Yangtze.
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: VARIATIONS IN EARLY LIFE HISTORY TRAITS OF JAPANESE ANCHOVY ENGRAULIS JAPONICUS IN THE YANGTZE RIVER ESTUARY
Review round: 1
Reviewer: 2

Output:
Basic reporting: The language and formatting need some improvements. Many words are fused as a single word and some sentences e.g. line no 37, 67-69, 91-92 can be simplified for clarity.
Experimental design: Authors aim to profile the distribution of Engraulis japonicus and their larvae to understand variations in their growth and life history traits. A few suggestions are listed below:

- It is not very clear when is adult fish data discussed and when is the larvae data discussed. This is confusing in both text and figures. It will be good to explicitly indicate larvae and adult related results for clarity in both text and figures. For example, is otolith analyzed from larvae, fish or both? How is the growth rate of the fish calculated.

- Line 118-120: cite the source of the data for other regions.

- The data on all the individual larvae should be provided as supplemental files. Also, the annotation of the supplemental file is not enough to understand the columns.

- Authors should also use a non-parametric method to compare frequency distributions.

- It will be great to include pictures of larvae and the fish if possible.
Validity of the findings: The manuscript is mostly descriptive and the scope may be very limited. The findings may be valuable for researchers or conservation biologists working on this specific fish. It will be great to discuss the implications of their findings for the conservation of this fish.
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: VARIATIONS IN EARLY LIFE HISTORY TRAITS OF JAPANESE ANCHOVY ENGRAULIS JAPONICUS IN THE YANGTZE RIVER ESTUARY
Review round: 1
Reviewer: 3

Output:
Basic reporting: The paper was generally written clearly, but both the introduction and discussion could be much more thorough. Please see my attached review.
Experimental design: The experimental design was appropriate and the study was carried out properly.  Methods used were well established and appropriate. I only have issue with the use of the biological intercept method in an area and on a population where otolith and somatic growth may be de-coupled. I discuss this more in depth in the attached review.
Validity of the findings: Here is where I think the manuscript needs further development. I don't feel the authors have thoroughly discussed the patterns they have identified. All the possible drivers of these patterns should be addressed and they should argue their hypotheses of why they found what they did.
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: VARIATIONS IN EARLY LIFE HISTORY TRAITS OF JAPANESE ANCHOVY ENGRAULIS JAPONICUS IN THE YANGTZE RIVER ESTUARY
Review round: 2
Reviewer: 1

Output:
Basic reporting: The manuscript, particularly the introduction is much improved.
Experimental design: No comments.
Validity of the findings: The findings will still be important for only Anchovy researchers, but given the importance of the fish for the region, they can be considered significant.
Additional comments: The authors have responded to my comments to satisfaction, and I have no further questions.


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: APPLYING FECAL MICROBIOTA TRANSPLANTATION (FMT) TO TREAT RECURRENT CLOSTRIDIUM DIFFICILE INFECTIONS (RCDI) IN CHILDREN
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper is well written, with sufficient background information and citations to relevant literature. Most of the tables and figures are meaningful and self-explanatory.
Experimental design: The research question is well defined and sufficient details are provided for replication of the study.
Validity of the findings: The statistical analysis is appropriate in most cases. The authors realize and discuss the potential limitations of the work and have relevant future directions.
Additional comments: Comments:
Please clarify why the single patient received nasal fmt.
Please clarify how were the donors assigned to patients.
Add few citations for line 55-56
Curious as to why family members were not selected as donors like in citation 25.
Line 206, please state the actual p-value
Line 165, please mention version of greengenes database
Lines 168-170, at what taxonomic level was beta-diversity calculated?
Kindly do one of ANOSIM, ADONIS, MANOVA test in place of lines 198-201. Don’t really see the use of Figure 2.
Line 230, provide a table showing the genera that showed differential abundance.
Please discuss how your design and results compare against the studies (citations) 23-25.
Please perform multiple testing correction wherever appropriate.


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

Input:
Title: APPLYING FECAL MICROBIOTA TRANSPLANTATION (FMT) TO TREAT RECURRENT CLOSTRIDIUM DIFFICILE INFECTIONS (RCDI) IN CHILDREN
Review round: 1
Reviewer: 2

Output:
Basic reporting: Human gut microbiome is an emerging area of research to investigate the role of microbiome in human healthy vs. diseased conditions. Clostridim difficile infections (CDI) are serious health issues leading to the deaths among adults and children. The infections are recurrent due to lack of efficient drug therapy. Fecal microbiota transplantation (FMT) is a novel therapy used to treat CDI but the therapy has been limited to the adults as far. This study shows, for the first time, the efficacy of FMT in pediatrics.
Experimental design: The specimen was collected from donors and study participants (age range from 21 months to 18 years) pre and 3 months post-treatment. The microbiome profiles of the donor and post-FMT patients were mostly similar whereas a significant difference was observed between microbiome profiles of pre and post FMT patient samples. The study, therefore, showed that the FMT significantly affected the gut microbiome compositions in all the patients.  There was also the significant increase in Bacteriodes: Firmicutes ratio post-FMT which is the indicator of the healthy gut microbiome. The difference in the microflora was observed at taxon and genus level.
Validity of the findings: The article is very well-written. The authors have properly examined the study participants for the number of earlier CDI episodes, symptoms, ongoing antibiotic treatments and disease symptoms before FMT therapy. Post-FMT follow up was also done carefully for 15 study participants. The results were consistent with the earlier findings reported in adults. The significant taxonomic shifts of gut microflora were observed in the patients post-FMT. The high abundance of Proteobacteria in pre-FMT profiles vs. high abundance of Bacteroidetes in post-FMT profiles was also consistent with the previous studies. However, there are some limitations in the study as self-mentioned by the authors which should be highlighted:
1)	The first limitation is the sample size which is very small to predict the efficiency and efficacy of the particular therapy and could be misleading. The study is properly validated and publishable only when the sample size is large (>100 samples).
2)	The diet and environment play a major role in determining the gut microbiome as shown in previous studies. These are not taken into consideration in this study. I suggest including the diet and environmental factors also in the study.
3)	A table showing the age, sex, diet, and present antibiotic status of the study participants should be there in supplementary data for making the study more informative for the readers.
Additional comments: In light of above comments, I suggest the authors to perform an extensive study on FMT with large sample size to prove this study highly relevant, impactful and publishable.


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: APPLYING FECAL MICROBIOTA TRANSPLANTATION (FMT) TO TREAT RECURRENT CLOSTRIDIUM DIFFICILE INFECTIONS (RCDI) IN CHILDREN
Review round: 1
Reviewer: 3

Output:
Basic reporting: This manuscript aims to answer questions regarding the efficacy of fecal microbiota transplantation (FMT) for recurrent C difficile infection (CDI) in children within the age range of 2-18 yrs. The authors demonstrate that administration of feces from healthy donors to the children with or without underlying IBD/Colitis reduces the incidence and recurrence of CDI and improves the livelihood mainly by increasing Bacteroidetes to Firmicutes, ratio post-FMT. The Methods, source of data and data abstraction, assessment, analysis are well described in the manuscript. Authors are commended for providing extensive raw data set, and thorough statistical analysis.
Experimental design: 1) 1.	The two important cohort study related to the FMT for rCDI could be included as they are pioneering studies
Russell et al., J Pediatr Gastroenterol Nutr. 2014 May;58(5):588-92. doi: 10.1097/MPG.0000000000000283.
Bakken et al, Clin Gastroenterol Hepatol. 2011 Dec;9(12):1044-9. doi: 10.1016/j.cgh.2011.08.014. Epub 2011 Aug 24.
2) Description of the donor age, gender in Table No.1 would be more informative.

3) Please include the specimen preparation for transplantation procedure in detail. Was the preparation done under ambient air or in the anaerobic atmosphere?

4) What was the stability of the FMT mediated engraftment of the microbial population?
Validity of the findings: The major limitation associated with the manuscript is the small sample size, It is unclear if findings are reproducible and credible due to real lack of association or small sample size.
Additional comments: 1)	What could be the predominant reasons behind increased incidences and recurrences of CDI in children in recent times?

2).	What was the donor age range? Is it advantageous to use a young FMT donor as compared to the aged one? Also, what could be the impact of matching the gender and ethnicity of the donor to recipients or vice-versa?

3) As the microbial flora of young children are considerably different than the adults, does the FMT from the adults to treat children affects the length of healing/recovery as compared to FMT from adult to adult?


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: APPLYING FECAL MICROBIOTA TRANSPLANTATION (FMT) TO TREAT RECURRENT CLOSTRIDIUM DIFFICILE INFECTIONS (RCDI) IN CHILDREN
Review round: 2
Reviewer: 1

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


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

Input:
Title: UNILATERAL APPLICATION OF AN EXTERNAL PNEUMATIC COMPRESSION THERAPY IMPROVES SKIN BLOOD FLOW AND VASCULAR REACTIVITY BILATERALLY
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper is well written, and easy to follow.
Experimental design: The experimental design is sound, and data appear to have been carefully collected. There are a few lines needing clarification:

In the study design, line 92-95, was the 30-min post FMD measures performed immediately following the EPC bout, or 30 mins later (i.e., 60 mins from start of EPC)?

Lines 102-105, was the sham simply a control, or were EPC cuffs positioned and not inflated? I know it is indicated elsewhere in the Methods, but please clarify here too.

Lines 142-143, include the version and company name for the FMD Studio software, I’m assuming QUIPU.
Validity of the findings: The authors back-up previous work from their laboratory in regards to the peripheral vascular changes following EPC. However, there are some recent reports that would be worth referencing in the manuscript:

Lines 174-176, what was the rationale for utilizing an EPC pressure of 70 mmHg? A previous report (Credeur et al. J Spinal Cord Med, 2017) used a pressure of 120 mmHg (Intermittent Pneumatic Compression—IPC), and found a localized improvement in leg vascular health. Is there a threshold pressure for improvements? Please elaborate, either in this section or in Discussion.

There is a fairly recent report (Rifkind et al. Nitric Oxide, 2014) which investigated the impact of leg IPC on systemic changes in NO-mediated markers, such as plasma nitrite, and vascular function in the arms. It would be worth incorporating this reference into your discussion of bilateral changes in leg FMD in response to unilateral EPC.
Additional comments: No further 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: UNILATERAL APPLICATION OF AN EXTERNAL PNEUMATIC COMPRESSION THERAPY IMPROVES SKIN BLOOD FLOW AND VASCULAR REACTIVITY BILATERALLY
Review round: 1
Reviewer: 2

Output:
Basic reporting: This is an interesting study on physiological response to local therapeutic tissue compression. The background may be, according to the authors, clinical requirements. Had it been like that, more justification would be needed. In the present form it is not convincing, at least for the  reviewer who  is a clinician. It might be better to focus  attention to purely physiological phenomena during local tissue compression.
Experimental design: The presented measuring methods have been chosen correctly and described  sufficiently.  What is lacking is a vague description of application of the compression sleeve. Were chambers inflated sequentially, how fast, distal to proximal pressure gradient? What was the skin temperature immediately after removal of the sleeve as it goes down within 1-3 minutes after exposure to ambient temperature. Another words, how much heat was produced by the inflating sleeve at the chamber-skin interface (mechanical to heat). How much heat energy was supplied to the investigated person by compression? How much heat energy was retained in the part of limb covered by the sleeve for 30 minutes? All this is easy to calculate. Heat generation and distribution process?
Validity of the findings: Compression  resulting in tissue deformation and  mobile tissue fluid mobilization provides energy which is fast dissipated all over the body due to blood perfusion and brings about a systemic response to heat energy input. Subsequently, heat excess is being eliminated in other parts of the body exposed to temperature lower than that of core tissues. No wonder that increase in temperature  through dilated skin microvasculature in the contralateral was observed. This type of "consensual" reaction  has been known for  long.
Additional comments: The problem of  increase of tissue elasticity  during therapeutic  limb tissue compression has been widely discussed. No consensus has been reached. Some consider it to be caused by  increase of  tissue temperature  (mechanical to heat energy) , others calculated  forces and found  that total heat  retained in tissues is negligible as it is immediately washed out.
The reviewer suggests:
1. Introduction: focus widely on physiology and not clinical aspects
2. Methods: add  more detailed  description of  compression
3. Results: try to calculate  the heat energy  balance during compression
4. Discussion: concentrate upon  heat balance  basing on the relevant contemporary literature


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: MIPHY: IDENTIFY AND QUANTIFY RAPIDLY EVOLVING MEMBERS OF LARGE GENE FAMILIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: Writing and organization were appropriate and professional throughout. Literature references were sufficient. Figures were adequate - Figure 1 was exceptional. Article was self-contained and generally presented well.
Experimental design: This article was basically a presentation of a new method for phylogenetic clustering of gene families, including method validation on 2 empirical datasets. The methodology was described in adequate detail and compared informally to other methods considering similar problems. No head-to-head method comparison was performed, which could have strengthened the results. Validation of the proposed method was not very formal, but mostly consisted of a description of how the proposed method 'correlated' with previous empirical results. The method validation analyses and discussion were adequate, but additional analyses - particularly more formal method evaluation using either empirical or simulated data - would strengthen the manuscript.
Validity of the findings: The proposed method was well-described. Validation of the method on empirical datasets was largely qualitative and would have benefitted from a quantitative assessment using benchmark empirical datasets or simulated data.
Additional comments: The proposed methodology will probably be welcome in the field and does advance the rather esoteric methodology of gene-species tree reconciliation. Method validation would have been strengthened by including a formal assessment on empirical data or simulated data (ideally both), but the informal method assessment presented appears adequate for a methods presentation 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: MIPHY: IDENTIFY AND QUANTIFY RAPIDLY EVOLVING MEMBERS OF LARGE GENE FAMILIES
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article meets all standards set by the journal. I have no comments to the structure and text besides three really minor points.

Line 232: Tg and Ts should be explained in the main text not only in the supplement.
Line 321: What does the measure U stands for?
Line 350: “…we could predict those with observable knock-ow phenotypes.” Could they specify how? Do they expect these genes to have always lowed instability score as in the case of collagens? If yes, could they explain, why they take this assumption.
Experimental design: The design of the study is clear and easy to follow. The method is described well in the manuscript and attached supplement, however I would like to ask for one important clarification. My lack of understanding may result from my poor understanding of some principles of the statistics behind.

Matter of clarification: I think that I understand in general, how the events are assigned to nodes and how the score is calculated for a node g. What I do not understand is, how the borders of MIGs are defined. As this is critical for the whole paper, I would be happy if the authors could explain this more explicitly for readers less trained in in mat and statistics like me.

The only imperfection of the tool, which I am able to recognise, is the fact that it does not take into account the robustness of the tree branching (measured e.g. in bootstraps). I would imagine that this feature would be useful particularly for assessing the events of incongruences. At this point they assume (Article S1, line 17) that “…incongruence is more likely than a duplication event followed by several independent loss events, so the latter is not considered as possible history.“ However, the latter is indeed a possible history, which should be in my opinion preferred over incongruence if the branch support for the daughter node(s) below the node of incongruence (n4 node in Figure S1) would be high.

The executables and testing file are provided and downloadable. The online web tool seems to be working as described. The graphical interphase is nice and easy to operate. The calculations are fast as stated in the manuscript.
Validity of the findings: The paper describes a tool for defining a sensible units (MIG) in a tree of large gene family and for quantification of “speed” of evolution within such units. As the phylogenetic analyses of large gene families is often un-easy, having such tool is by all means a sensible idea. They provide analyses of two gene families, which apparently support the usefulness of the software. Future and other users will assess the value of the tooll in their targeted analyses. To me, the tool seems functional, the interface is well-arranged, interactive and easy to operate. However, I was testing it only on the testing data sets provided by authors. I would recommend using the software for analyses of large gene family phylogenies.
Additional comments: I propose minor revision but I feel it is actually very close to "accept".