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: UNCERTAINTY AND SENSITIVITY ANALYSIS OF THE BASIC REPRODUCTION NUMBER OF DIPHTHERIA: A CASE STUDY OF A ROHINGYA REFUGEE CAMP IN BANGLADESH, NOVEMBER–DECEMBER 2017
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors present an interesting and well-structured paper, yet there are several areas where additional refinement is required.

Throughout the paper there is writing that can be made more concise and clear. At points, the writing needs substantial clarification. For example, the description of the case definitions and their changes was not clear –the case definition after 11 Dec was detailed, but it is not stated what the definition was prior. Additionally, correct punctuation is missing throughout. For example, a comma [“,”] should often be used before the word “including” when you are listing examples, etc. (see lines 62, 82, 246

Literature citations are generally sufficient throughout, with the exception of one key citation. The authors present their model, yet provide no background on its previous use, reason for use, etc. They also do not explicitly state that they developed this model, nor do they provide any defined validation of this model. Upon searching, I found a previous paper proposing this model, by the senior author (Nishiura Int. J. Environ. Res. Public Health 2010). The author should revise the methods to reference this work, and explain why this model is being used in this context instead of other options, such as the epidemic growth model.
Experimental design: This article presents original primary research that is within the Aims and Scope of PeerJ. The research question, that of estimating the R0 for diphtheria in a modern context, is relevant and meaningful, and fills an important gap in knowledge.
The analysis performed is of high technical and ethical standards, however there are some major flaws in the design and/or description and purpose of the authors’ methodological choices.

The first problem is the general description of the methods and layout of the methods section. As presented, they are not well structured and lead to substantial confusion and questions. The methods start off with a definition of 2 parameters, i and g, then lead into a lengthy description of g. This is before we are presented with any model or basic framework. This type of information should go after the model is presented.
Next, the readers are given the model, but without any explanation of the choice of the model and derivation of it. As stated above, this renewal process model is defined in the methods, though there is no background provided on why this model is being used, how it was developed, how it is valid, etc. As is reads, it is unknown whether the authors developed this model for this work or they believe that this is a well-known model that they are just applying. In either case, this should be stated. From what I found in the literature, they did not develop this model for this work, as it was previously presented by Nishiura in 2010.

Another major problem is their choice of prior distributions for unknown parameters, and their descriptions of these. As they state, they defined the sampling distribution for v, the vaccination coverage, with a triangular distribution from 0-0.7 (line 149). However, they also state in the same sentence that a previous survey found that 30.8% of children had received no vaccinations (line 150), thus according to that survey, 69.2% had received vaccination. Given that it is well documented that diphtheria has among the highest coverage rates of vaccines, it can be presumed that if this survey is correct, I would have expected the authors to set a prior for v such that the mean prior distribution is at ~70%. Instead, their prior distribution has a mean of 35%, and does not allow v to go above 70%, which is possible, given vaccination coverage among adults may be substantially higher than that among the surveyed refugee children.

Additional to the problem with the distribution allowed for v, there is no mention of what distributions were allowed for alpha1 and alpha2. It can be assumed they used LHS to determine the values for these parameters along with v, but there is no mention of what values or distributions were used. In general, the authors need to provide a clear and concise description of the input variables and parameter values/distributions inputted into the model. This should be noted in the methods, and it would be useful to have a table of this information.
Validity of the findings: There is no mention in the Results section of the estimation results for v. This is actually presented in the discussion, though it is not detailed (i.e., no range, confidence intervals, etc.; line 221). At the very least, this should be moved to the results and additional information should be added.

I also do not understand how estimates of alpha1 and alpha2 were so different, particularly given there was no dramatic change in the number of reported diphtheria cases around December 11. If these parameters were as different as these estimated values say, there should have been a notable change in the epidemic curve, demonstrating a district change in case ascertainment. Furthermore, the hyperbolic relationship between alpha1 and R0 does not make sense, and the authors’ reasoning that it occurs because alpha1 crosses 1 does not justify this relationship (line 177). Why would alpha1 go from 0.02 (i.e., ascertainment of 1/50 cases) at R0=8 to >1 at R0>8.5? It seems that there are some misspecification sampling issues occurring.

I have some concerns that the problems with the parameter distributions state in the “Experimental Design” section of this review may be influencing the results of this study. Specifically, the finding that the median R0 for this outbreak was 5.8, which correlates directly to the mean/median/mode of the v  input distribution of 35%, given my above concerns that this is a misspecified prior (given prior knowledge from both the survey and DHS). This may very well be a correct estimate, but I would like to see this analysis redone with a more appropriate set of parameter priors.

Additionally, I would have liked to see a brief mention or discussion of the possibility that case ascertainment of the last several days/weeks of the case data may be inaccurate due to reporting delays. It is highly likely that in a setting such as a refugee camp, and especially in an outbreak as such, that reporting of cases would be delayed substantially.
Additional comments: This is an interesting and timely analysis. I believe if these problems detailed here can be addressed, it will provide useful additional information on diphtheria in the literature. I have provided some additional grammatical edits and minor comments in the PDF of the manuscript, as well as these listed below. I would recommend spending some time to clarify some confusing sentences, make the writing more concise, and recheck for grammatical errors.

Specific comments:
Line 45. Please revise this to be more concise and clear. Additionally, the grey or white patch causes the "croup".

Line 102. It needs to be made clearer what data times and number of cases were included in this analysis. Please state this all together.

Line 114. As Nishiura is an author, these seems like an invalid reference. Please reference previous use of this, or use a brief explanation of it.

Line 132. This is confusing. Is this N=579,384 just the epidemic area within the refugee camp, or is this the population of the entire refugee camp. Also, this can be rewritten more concisely.

Line 135. What does tau represent in equation 4? I found it in Nishiura 2010 representing time since infection. Is this correct here too? This needs to be described.

Line 194. The authors state that: “This dependency [R0 and alpha2] is anticipated, because R0 would influence how many susceptibles to be depleted to curb the epidemic curve and that is regulated by the value of a2.” Why is this regulated by alpha2? Alpha is a parameter of case ascertainment and does not have any bearing on the disease process. Please clarify this.
Line 225. The authors state that “It is remarkable that ascertainment rates were jointly estimated only by using the epidemiological case data and the population size.” I would argue that this is not necessarily remarkable given that ascertainment rates were not actually estimated with any accuracy. Then presented estimates of alpha1 and alpha2 are qualitatively different, despite lack of evidence for this in the epidemic curve or other knowledge. Additionally, the confidence ranges for these estimates are enormous.

Line 229. I would be very hesitant to state that this is the peak given these data are so recently reported. In outbreak and refugee settings, it is very common that large reporting delays occur, so it is possible that the leveling-off of cases is merely a factor or reporting delay.

Figure 2. Because alpha1 and alpha2 are reporting proportions that can be greater than or less than 1, these axes should be reported in log-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: UNCERTAINTY AND SENSITIVITY ANALYSIS OF THE BASIC REPRODUCTION NUMBER OF DIPHTHERIA: A CASE STUDY OF A ROHINGYA REFUGEE CAMP IN BANGLADESH, NOVEMBER–DECEMBER 2017
Review round: 1
Reviewer: 2

Output:
Basic reporting: The basic reporting is well done. You may add some references or sources of information on the vaccination campaign, for instance how do we know that the coverage reached was 90% (administrative coverage or survey?).
Experimental design: Well done
Validity of the findings: Constant Ro :
You state  in the introduction (line 62) that  “Due to vaccination effort and other countermeasures including contact tracing and hospital admission of cases, the epidemic has been considered to be gradually brought under control ….”. In the methods (Line 101), you justify why you have not include the effect of the vaccination campaign in your model. But the effects of the other countermeasures are not discussed. While vaccination does affect only the effective reproductive ratio, contact tracing, rapid hospitalisation and prophylaxis given to the contacts may have changed the basic reproductive ratio. The assumption of a constant Ro overtime needs to be discussed. Furthermore it would be interesting to explore a varying Ro, as you have included 2 ascertainment rates, would it be possible to include 2 Ro.  Knowing that the Ro was constant or changed overtime has some implication in your estimate, and it would inform the public health actors in the best strategy to control outbreaks (vaccination, prophylaxis, treatment and isolation).

Low CFR and partial immunization :
Compared to other epidemics (Recent Outbreaks of Diphtheria in Dibrugarh District, Assam, India; Diphtheria outbreak in Lao People's Democratic Republic, 2012-2013; Diphtheria outbreak with high mortality in northeastern Nigeria) the outbreak in Cox bazar had a much lower Case Fatality Ratio (27/2526 =1%). A number of reasons could explain this: a good case management (this is unlikely in this setting at this stage of the emergency), deaths were not recorded either because they died after discharge (they kept them hospitalized 48 hours only, which is short for diphtheria) or they died in the community unnoticed, low specificity of the case definition and low fatality of people with partial immunization (not having received the complete course of vaccinations, see “Epidemic Diphtheria in the Republic of Georgia, 1993–1996: Risk Factors for Fatal Outcome among Hospitalized Patients”). The latter reason is likely in this setting, I wonder if this would affect the model; It might deserve to be discussed.
Additional comments: It is an interesting article, that would be useful for health actors.


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: UNCERTAINTY AND SENSITIVITY ANALYSIS OF THE BASIC REPRODUCTION NUMBER OF DIPHTHERIA: A CASE STUDY OF A ROHINGYA REFUGEE CAMP IN BANGLADESH, NOVEMBER–DECEMBER 2017
Review round: 2
Reviewer: 1

Output:
Basic reporting: The author has sufficiently improved the manuscript from the the previous version. It is currently up to the standards of PeerJ for publication.
Experimental design: No comment
Validity of the findings: After the revisions and redo of the analysis, the findings appear to be valid.
Additional comments: Te edits have made this paper much easier to read and fixed validity issues. Very nice work. I have attached an annotated PDF with a couple additional minor edits.


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: UNCERTAINTY AND SENSITIVITY ANALYSIS OF THE BASIC REPRODUCTION NUMBER OF DIPHTHERIA: A CASE STUDY OF A ROHINGYA REFUGEE CAMP IN BANGLADESH, NOVEMBER–DECEMBER 2017
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comments
Experimental design: No comments
Validity of the findings: No comments
Additional comments: The authors well responded to the comments of the first revision.


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

Input:
Title: A WALK IN THE MAZE: VARIATION IN LATE JURASSIC TRIDACTYL DINOSAUR TRACKS FROM THE SWISS JURA MOUNTAINS (NW SWITZERLAND)
Review round: 1
Reviewer: 1

Output:
Basic reporting: This is a very well written and well documented study. My only concern is that it is simply too long and exhausting to read, but as I have a hard time pointing out specific sections that could be omitted, without weaking the argumentetion I will recommedn it for publication in its present form, as PeerJ has no page limitations.
The figures are well executed and are all nessecery to support the results presented in the paper.

I have not cross checked the refernce list.
Experimental design: no comment
Validity of the findings: no comments
Additional comments: This is a very well-executed piece of research and it clearly demonstrates how usefull a tool  3D photogrammetry has become  in palaeoichnological imterpretations.


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

Input:
Title: A WALK IN THE MAZE: VARIATION IN LATE JURASSIC TRIDACTYL DINOSAUR TRACKS FROM THE SWISS JURA MOUNTAINS (NW SWITZERLAND)
Review round: 1
Reviewer: 2

Output:
Basic reporting: The English grammar used through the manuscript is clear and professional. Although, some sentences and expressions could be improved in order to sum up the most important statements. I made a few comments on the pdf version. However, as I am not a native English speaker my grammar corrections are limited. Please consider a final check by a native speaker or a grammar expert.

The introduction and background are well presented and completed with actualized literature.

The figures are relevant, high quality, and well labeled. Although, I found figure 1B to small so it is difficult to read it, and a label in red color for no apparent reason on figure 6. Both comments are also included on the pdf version.

The raw data is supplied.
Experimental design: The research is original, with primary data analysis. The research questions are clearly stated, relevant, and meaningful and followed throughout the manuscript.  The technical methods used to analyze the data are modern, proper and well described to replicate it.
There are some comments on the approach of the morphotype variation due to ontogeny. See below.
Validity of the findings: The manuscript is a good example of how to analyze in detail the ichnological record of a unit plentiful of tracks and trackways with similar morphologies preserved. The authors evaluated the shape variations of footprints along trackways and between morphotypes, the possible ontogenetic relationship between them, evaluate its ichnotaxonomy to finally contribute to the faunistic composition of the ichnoassemblage.
The most important comment is on the discussion about morphology variations due to ontogeny (lines 397-492).  The authors explore to lines of thought 1) variations in morphology, 2) spatiotemporal relationship. The second line of thought is perfectly well stated. I find some problems with the first one.
On the first paragraph (lines 398-423) the author mentioned different criteria used by other authors to evaluate ontogenetic variations. One seems to involve morphologic variations on footprints due to allometric growth of individual as the Grallator-Eubrontes plexus suggested by Olsen, 1980; Olsen, Smith & McDonald, 1998; Moreau et al., 2012(lines 401-410). The other involves linear growth (lines 420-423).  On the following paragraphs the author analyzed the small tracks from the Swiss Jura Mountains. Those paragraphs are confusing sense they do not express clearly which kind of growth they expect to find (isometric or allometric). Besides, results somehow difficult to read because it abounds in descriptions and comparisons but lacks of sentences that clearly summarize the conclusions arrived. See as example the comment about the paragraph (424-443) on the pdf version. In that sense, it would help to state more clearly the lines of thought and to reinforce the discussion with sentences that sum up the most important statements. I consider these are important modifications due to the topic is of high interest and has been only superficially aboard on the ichnological literature.
Other minor comments are expressed on the pdf version.
Finally, the conclusions are well stated and linked to the original research questions.
Additional comments: no comment


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

Input:
Title: DETERMINING THE NUMBERS OF A LANDSCAPE ARCHITECT SPECIES (TAPIRUS TERRESTRIS), USING FOOTPRINTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article generally meets these requirements. I suggest some minor revisions below, which I would expect the authors would easily implement, and which address any concerns on reporting.

Line 42: ‘the South and central America’; delete ‘the’
Line 99: “for censusing’ or “to census’
Line 150: ‘under’ the footprint is not what you literally mean, as Fig. 2 shows. Perhaps, ‘alongside one of the ruler’ is clearer.
Line 170: about ‘the’ FIT algorithm
Line 180: what level of accuracy was achieved with the test data? This fact is an important detail.
Lines 183 – 195: This text is a little confusing. As I understand it, 15 landmarks are chosen on anatomical grounds to yield repeatable measurements between these landmarks. A script then yields a further seven derived points and a total of 121 measurements based on these 22 points are computed. These 121 measurements are intended to include all measurements that might prove useful in discrimination. All of this procedure occurs before any data, other than a generic tapir footprint, is examined. The training data is then employed to select the measurements amongst the 121 that are most effective at discrimination, yielding the ‘tapir’ FIT algorithm, which can then be applied to field data. The construction of the algorithm needs to be more clearly separated from its application to field data.
Line 206: ‘at’ several different scales
Line 223: ‘more’ than what? Or do you mean area A had the most tapirs?
Line 225: ‘represented’ rather than ‘presented’
Line 226: State the results for areas B and F here, as well as referring the reader to the Supplementary Figures.
Lines 231 – 232: ‘The other sites, when combined, did not indicate any individuals visiting more than one area.’

Line 235: Explicitly indicate what the response variable y is (presumably number of tracks) and the predictor variable x is (presumably number of tapirs). Replace ‘Rsq’ by ‘R2’

Lines 240 -242: This statement is too strong. Rather, you are relying on FIT’s identifications too infer tapirs visit several locations. Given that you do expect tapirs to do so, the fact that FIT did indicate so is a reassuring outcome but it is not proof so much as consistency with expectations. FIT, as with any estimation procedure, provides confirmation on test data but inference on field data.

Line 245: Again, the FIT analysis infers long-range movement, it does not demonstrate it, in the same was as say radio tracking would. Footprints are no 100% unambiguously identifiable so you do not have unambiguous evidence of such movement, but rather inference based on an estimation procedure. I emphasize this point not to undervalue the approach but to be precise.

Line 250: This result indicates…

Line 261: The extent to which the dirt roads sample the tapir habitat is an important one. Can you say a little more about whether the 70 dirt roads would provide adequate coverage to sample tapir activity using FIT in this area? More generally, is FIT practical on other than dirt roads for tapir, e.g., on game trails?

Line 268: ‘trackers’ expertise’ or ‘tracker expertise’

Line 276: for the regression of tracks on tapir numbers the effects of sampling intensity and other factors might be incorporated into a more complex model. I agree it would require rigorous testing, though it may be useful as an index.

Lines 382 – 383: This citation is incomplete, the journal title is missing
In table 2, the entry ‘A+B” needs to be lined up with its data better.
Experimental design: A reader would need to consult the references provided by the authors on the method FIT employed in this paper to fully understand the method. Given the previous publications on this method, referenced and amply cited in this paper, I think this approach is appropriate in this paper.
Validity of the findings: Minor concerns regarding statements of conclusions are detailed in the minor revisions recommended to the authors in section 1.
Additional comments: The paper provides another example of the application of the FIT method, further demonstrating its utility for ecological and conservation science. The tapir is an interesting example since its footprint is rather unlike the other examples reported so far. The ecological role of the tapir and its challenging environment adds further value to this study.


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: DETERMINING THE NUMBERS OF A LANDSCAPE ARCHITECT SPECIES (TAPIRUS TERRESTRIS), USING FOOTPRINTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: In general the paper is well written and organized. Some editing is necessary for proper English. The following are some examples, but others are likely. Examples are keyed to line numbers:
	18 - populations not population; ecosystem not ecosystems
	42 - in South not in the South
	46 - “lowland tapir populations are” not “the lowland tapir population is” unless you saying that there is only one population in Brazil
	53 - “like” is not correct usage
	54 - plant not plants
	61 - individuals not individual
	67 - is essential not are essential; “tapirs are” not “the tapir are”
	99 - “to census” not “to censusing”; but actually, a census implies a complete enumeration of individuals
	233 - data were not data was
	268 - trackers’ not trackers
	269 - species’ not species

Other items that need correcting/changes:
	25 - you use “Footprint Identification Technique” here and in lines 3 and 82 (maybe elsewhere);  the picture of the webpage as well as Table 2 uses “Technology” not “Technique”; seems surprising given that the software designers are listed as authors
	79 - actually, tapir images from camera traps can sometimes be separated to individual on the basis of scars, scratches, and other marks; such marks may not necessarily be permanent but may be sufficient for separate sample periods
	90-94 - scientific names of all additional species are needed
	138 “after dusk and dawn” is vague

	Table 2 - says there were 440 total footprints and 46 total trails; the results (line 215) says 547 footprints and 48 trails; also, the numbers in parentheses are not explained in the table heading; the column heading “Estimated number of tapir” should be “Estimated number of tapirs”; the data for line A+B are offset one line up
Experimental design: The description of the methods is clear and well described; there are no experiments per se.  The results of the study depend on the validity of the technique used (FIT). From the literature cited, it appears that the method has been used for a variety of species. It also seems that the software designers were part of virtually all the studies. To be completely convincing, some independent tests of the technique would seem reasonable (i.e., can the same results be obtained by someone else); on a related note, it would be good to know if the software will be made available - either open access or for a license fee.
Validity of the findings: Assuming the technique is correct, then the results appear reasonable for this particular site. As mentioned above, some independent tests would be useful. On lines 183-187, the method description states that 15 landmark points are selected - if different people select the landmarks, are 1) the same landmarks always selected and 2) are the results the same. From the description of the site and the images provided, the road surfaces look fairly ideal for tracks. On the other hand, tapirs in most areas likely do not  have the option to walk along roads and, instead, walk along trails within forests. Often those trails may be  very different surfaces, frequently muddy and frequently of different “hardness”. Consequently, tapir tracks in muddy surfaces would look very different. To extend the validity of this study beyond the specific site, comparisons with results from different sites and different surfaces would be necessary.
Additional comments: It is stated that the FIT allows one to distinguish individuals, sex, and age but only number of individuals is reported. Were you able to distinguish sex and age and, if so, why not report those numbers (if you were not able to, it would be useful to know that as well). On a somewhat related point, on lines 280-282, you suggest that a goal is a long-term study on tapirs in the area (a very valuable goal, indeed). A long-term study would, presumably, cover individuals from young to adult ages, with, presumably, considerable changes in footprints - do you know if an individual’s footprint can be distinguished no matter the age? or do the footprint characteristics change with age? This would be important for long-term demographic studies.

Lines 259-260 - This is an important caveat: “With appropriate weather conditions and substrates, and a moderate sampling effort, footprints can be used effectively for censusing tapir populations.” It might be useful to expand a bit on this point - particularly with respect to substrates that tapirs typically encounter.


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: SIMULATED DISPERSER ANALYSIS: DETERMINING THE NUMBER OF LOCI REQUIRED TO GENETICALLY IDENTIFY DISPERSERS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is well written and easy to understand. However, there are some sentences that are not logical structured. For example:

lines 55-56: An individual genotype cannot be similar to a population. It can only be similar to another genotype randomly sampled from another population.

lines 157-159: I’m not sure I understand this. In line 154 it is stated that the explanatory variable is “the population in which the simulated disperser was located”. Although this statement is ambiguous, I assume this means the population where the individual was sampled in reality before being “artificially translocated”. But then it is stated that “location was specified as a categorical variable with four levels (…)” I really don’t understand how this explicative variable was coded. This needs to be better explained.
Experimental design: The authors propose an original procedure to validate the results of studies that estimate dispersal using genetic markers. In a nutshell, the validation consists in using the data to carry out “experimental” translocations of individuals among sampled populations and then carrying out assignment tests to estimate error rates. I think this is a useful way to evaluate the reliability of the results obtained by a given study and, therefore, it is a valuable contribution. However, the use of this procedure cannot prevent or correct errors in the sampling protocol used to obtain the dataset. This is something that should be discussed.
Validity of the findings: The findings of this study are consistent with those of previous studies but also provide some new insights (e.g. number of loci necessary for obtaining reliable estimates is larger than those suggested by previous studies).
Additional comments: Overall, this is a study that will help improve the quality of studies focused on dispersal. Besides the issues I highlighted above, there are two other main issues that I would like to authors to address.

a) Clearly, the proposed approach is only aimed at verifying that the dataset and method of choice can indeed provide reliable results. This is fine but ideally, one would like to have some idea about the sample sizes and number of loci needed to obtain reliable estimates before carrying out the field work needed to collect the samples. The proposed procedure cannot address this problem, only a preliminary “true” simulation study (i.e. based on synthetic samples) can help in this regard particularly in terms of sample sizes needed. I think the authors should discuss this issues in much more detail.

b) The literature search aspects of the study are poorly addressed in the current version of the manuscript. For example, it is not completely clear why the authors want to carry out an analysis to investigate the relationship between genetic differentiation and number of loci used. This only becomes apparent later on (c.f. lines 276-279). The authors should explicitly state the motivation for this analyses much earlier on (e.g. lines 174-176).

Other comments:

lines 267-269: How can you explain the fact that a locus with high PIC leads to erroneous results?


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: SIMULATED DISPERSER ANALYSIS: DETERMINING THE NUMBER OF LOCI REQUIRED TO GENETICALLY IDENTIFY DISPERSERS
Review round: 1
Reviewer: 2

Output:
Basic reporting: This ms. is clearly written and carefully proofread (for which I'm grateful!); lit references and background are adequate and the authors clearly describe the limitations of their analysis, with some minor exceptions noted in my comments to the authors.  Raw data are available and the results are relevant.

Fig. 4 and its associated analysis are perhaps a response to previous reviewers arguing that the manuscript is no longer relevant since other methods of identifying immigrants (not based on microsats) are available.  I agree with the authors that microsat-based analyses are likely to continue, and so don't think this analysis and figure is necessary.
Experimental design: This manuscript addresses an important issue related to the use of microsatellite loci to identify interpopulation dispersers via genetic assignment tests.  Such tests have long been known to "pick up" dispersers' descendants as well as the dispersers themselves (and of course there may also be "false negatives" and "false positives" of the sort expected in any statistical comparison). But few users have noted or attempted to evaluate the magnitude of this problem as it applies to their particular study system.  This manuscript describes one approach to doing so, and it does a good job.  I have two suggestions that I think could increase its value to readers:

1)  As the authors note, their analysis applies only to their 3 populations, or perhaps to another set of populations with a similar level of differentiation.  The conclusion that "at least 27 loci are needed" would not, for example, apply to a system with higher Fst.  In this or future publications, I'd encourage the investigators to provide readers with more guidance about how to deal with the issue themselves.

In particular, could they provide the R code that an investigator dealing with a different set of microsats, or a different set of genotypes, would need to generate the equivalent of figure 2?  Or, if they are suggesting the more "seat of the pants" approach outlined in fig. 5, can they suggest either how to choose the "test dispersers" in their simulation approach so as to maximize the possibility that they include the worst-case individual?

2) As the authors indicate, dispersers can be misidentified in two ways, false positives and false negatives.  The paper would be more useful if the two types of misidentification were addressed explicitly.  As I understand it, the response variable in the statistical model (and fig. 1) specifically addresses only the problem of correctly identifying dispersers as such (lines 149-152).  Is it possible to generate a parallel analysis (and plot) dealing with the probability of correctly identifying a nondisperser?  In other words, if I started with the microsat genotype of a an individual that was actually born in population A, how many loci would it take to be sure (at some level of probability) that GeneClass would not misclassify it as an immigrant to that population?
Validity of the findings: The analyses seem to me appropriate and clearly described, with some minor caveats noted in comments to the author.  See comments above.
Additional comments: In addition to the major concerns listed in section 2, here are some secondary issues --

Line 67 fix font of “populations”

Line 70-71.  Another extensive comparison of mark-recapture vs. assignment test vs. parentage analysis approaches to identifying dispersers is Waser, PM and JD Hadfield.  2011 (How much can parentage analyses tell us about precapture dispersal?  Molecular Ecology.20:1277-1288).

A more obscure reference that used simulations to explore a similar question is Waser, PM, D Paetkau and C Strobeck. 2001.  (Estimating interpopulation dispersal rates.  Pp 484-497 in JL Gittleman, SM Funk, DW Macdonald and RK Wayne, eds. Carnivore Conservation.  Cambridge University Press).

By the way, a broader set of simulations exploring the probability that dispersing animals (and their descendents) are detected by assignment tests as a function of number of loci, mating system, and other population parameters is still available in an unpublished manuscript (still available at http://bilbo.bio.purdue.edu/~pwaser/genetix/download.html , where you should also be able to download the simulation code).  Though >20 years old, if this effort seems of use to the authors I’d welcome their use of it.

Lines 106-107: “These data were combined..”

Line 114: “better than Fst at handling…”

Line 124:  Clarify: was ONE randomly-chose individual in each population involved in all of the simulations?  If so, then are the quantitative conclusions essentially based on an N of 3?  Wouldn’t it be better to repeat this procedure with multiple individuals?

 assigned Line 126: “ being simulated dispersers..”

Lines 131-136: hard to follow, this needs to be broken into several shorter sentences.

Line 141: “an individual can incorrectly be identified as a disperser..

Line 143:  The term “misassignment” is inherently confusing (a misassigned individual is one that is assigned to its birth population, rather than the population it’s captured or sampled in, so if you’re interested in dispersal, it’s in fact correctly assigned… I’d urge the authors to purge all uses of this word from the ms, and just to delete this sentence. Instead, tell us how this analysis deals with false positives and false negatives (and preferably discuss both of them)

Line 144: The authors should consider expanding this sentence so as to more clearly separate what I think are two slightly different ways of thinking about the problem: correctly identifying an individual as a first-generation immigrant (rather than a “resident”), vs. correctly identifying its population of origin.  Both are discussed in this manuscript, but I think many readers will not immediately recognize that they are not exactly the same question.

Line 145: “In our assessment of the ability of GeneClass2.0 to detect simulated migrants, assignment tests were repeated..”
Line 150:  Would the results be different if the response variable were “population of origin correctly identified (yes, no)”?

Line 189ff; Mention the range of PIC values?

Line 205: see comments above about clearer (and separate?) analyses of the effect of number of loci on false negatives and false positives.

Line 206: “from its collection”

Line 215: “were needed to assign SD-B.. (use “assign” rather than “identify”

Line 218: the term “misassigned” is confusing, I’d delete this sentence.  Or perhaps say something like “misassigned as a resident rather than as an immigrant”?  More generally: this individual is puzzling and interesting – would simulating dispersal by a broader range of individuals indicate how often this pattern occurs?

Line 226: delete ‘up”

Line 231: excess “precision” given the sample size :  “on average 11.2 +/- 5.1 loci.

Line 256 How did the authors arrive at these numbers (“at least 15”)?  Can they suggest a quantitative approach, given their fig. 2?

Line 320: I appreciate the sentiment, but this sort of took me aback.  Why were any starlings killed:  was the sample a “byproduct” of some sort of control program?  If so, mention briefly in the methods.

Fig. 1: Fig. 4: “Piry et al. 2004”  -- but I’m not convinced this graph is necessary.

Fig. 5: I’m puzzled by step 1, “identify # of genetic populations”.  In the authors study, thy started with 3 samples, which (like most investigators) they label as “populations” without actually knowing whether they are in fact separate genetic populations in some idealized population genetics sense.  In contrast, some assignment routines attempt to infer separate populations from the overall sample of genotypes – better to either delete this step from the figure, or explain it in the legend or text.

Overall -- a nice "seat of the pants" approach, perhaps not statistically sophisticated but far better than ignoring the problem!

Peter Waser


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

Input:
Title: THE VALUE OF CITIZEN SCIENCE FOR ECOLOGICAL MONITORING OF MAMMALS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The writing is clear and unambiguous and in general the paper conforms to a professional article structure. Raw data are provided and I could open the files.
The submission is not self-contained because it relies on data and analyses from other units of publication (Kays et al 2016, Parsons et al 2016).
The paper does not address hypotheses directly. Rather it uses 2 case studies to make the argument that citizens can collect data at an acceptable standard to answer management questions and monitor mammal activity. Mammal activity is not defined initially and, at first I thought the manuscript might be about activity rhythms, but it became clear that ‘activity’ referred to encounter rates or detection rates and that detection rates were ultimately used as an index of abundance. The first study seeks to quantify black bear activity inside Carl Sandburg Home NHS to help inform bear management in the area. They compare bear activity inside the NHS, near the NHS and to other sites in the region. The second case study aims to document how mammal species were using the Prairie Ridge nature center over time, including species interactions, and to determine the effect of active prairie restoration on the mammal community. There were education and outreach goals as well, including involving visitors in scientific research, improving knowledge of mammals, and improving understanding of urban wildlife.
Experimental design: Camera trap surveys: Both case studies use standard camera trapping protocols and attain reasonable intensity of sampling effort. The changes in sensitivity and camera models were documented. Both studies use detection rate (DR, defined as independent encounters) as the activity/abundance metric.
Volunteer recruitment and training: Adequate. The Prairie Ridge survey suffers from small sample sizes that make statistical comparisons and conclusions difficult.
Data collection and verification: There is little description of how data entry and verification was actually carried out.
Analyses: The analysis rests on use of DR to make comparisons of species spatially and temporally. The authors argue that use of DR is justified because sites were selected at random relative to animal movements and were not baited and cite Rowcliffe et al. 2013 as justification. Rowcliffe et al. 2013 is a clarification about assumptions underlying the random encounter model and does not make mention of detection rates. Strictly speaking the camera trap placements were not random because they used rules to avoid clustering the traps, and it is unclear whether they considered placement of cameras outside the target site on properties of volunteers only or on all properties in surrounding neighborhoods. Use of DR in place of abundance has been criticized when making spatial and temporal comparisons because detection probabilities can change over space and time while DR use assumes the DR remains constant. Several studies have shown, however, that DR can be a good surrogate for abundance, especially for species that are territorial and for species that move alone or in small groups.
Validity of the findings: Monitoring and management: The comparisons in Figure 2 confound spatial and temporal comparisons. There are many reasons for the observed differences but the authors only report that differences exist. Figure 2 stacks 15 species from Sandburg House in a bar chart that is unreadable. The results in Figure 3 for Sandburg Home bears report a significant difference but do not provide statistics or the nature of the test and multi-site comparisons are not described in methods. The Prairie Ridge result that DR was almost twice as high as forested sites nearby was not evaluated statistically and could arise due to a difference in detection zones – cameras set in forests tend to have smaller field of view that cameras set in open situations. Finally, the presentation of results for DR, trends over time, trends over space, and resident versus non-resident species in a single paragraph is confusing.
There is no discussion of the accuracy of classification by volunteers and of how much time was required by the scientists to clean up the data before archiving and use in analysis. There is discussion of management outcomes, only the results of monitoring.
Education and outreach: The Sandburg House results are not actually a part of the study as described in the methods and should be moved to the discussion. The results of the survey at Prairie Ridge are not derived from tests so we do not know if the changes described are significant rather than anecdotal.
Additional comments: While I believe many of the statements made in this manuscript regarding the effectiveness of citizen science and the widespread merits of involving citizens in the scientific process, this manuscript does not present a convincing argument. As I have pointed out, the methods have issues that require clarification and in the case of the interview survey, the sample sizes are too small to draw conclusions. The results do not necessarily apply to management because they do not get to the heart of monitoring – why changes are occurring. As reported, there are several possible explanations for why the results appear as they do, and the experimental design does not attempt to clarify which explanation is correct. The bear results are interesting but only help to inform public perception rather than management of bears. The title speaks of the value of citizen science to monitoring wildlife but does not describe that value other than that volunteers reduce the cost of doing science. This is a valid point, but one that has been made more strongly by some of the authors in Kays et al. 2016.


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

Input:
Title: THE VALUE OF CITIZEN SCIENCE FOR ECOLOGICAL MONITORING OF MAMMALS
Review round: 1
Reviewer: 2

Output:
Basic reporting: I find this paper to be well-organised and easy to follow, and I am thankful for the opportunity to provide this review. The authors clearly described the need for more comprehensive ecological monitoring and how the challenges facing its implementation could be addressed through citizen science camera trapping. The figures and tables are also appropriate and helpful.

Some minor suggestions:

1. (Introduction lines 69-77) Citizen science is a broad term that is often misunderstood to only mean the crowdsourcing of data collection and classification. I suggest one or two sentences defining citizen science for the purposes of this paper while acknowledging its wider meanings for engagement and empowerment (such as, but not limited to, Haklay (2013): https://doi.org/10.1007/978-94-007-4587-2_7). While this study indeed focuses on data collection and classification, I think it is useful to say that citizen science is more than just that to prevent this misconception.

2. (Introduction line 98, Materials and Methods lines 124-125, Figure 1) Since this paper is being published in an international journal with a diverse audience, it should clearly report the study sites as being in the United States in the first instance. The map in Figure 1 should include an inset that puts the state of North Carolina in wider geographical context.

3. (Figure 2) I find it hard to read Figure 2 and differentiate the 16 species. It might help to separate it into two halves (e.g. Figure 2 a and b) that are identical except each half shows only eight species (i.e. eight species in each stack).  This way, colours (and/or patterns) can be reused between the two and be chosen for greater contrast and colour-blind accessibility.

4. (attached dataset) I was able to access the raw data attached with submission of this article. Including the full dataset is a crucial part of ensuring research integrity and reproducibility and it is exemplary that the authors have done so. However, while most of the column names in the data spreadsheet are self-explanatory, some are not clear to me. I suggest including a “readme” file with the data describing the meaning of each column, how they are derived (if they are derived data), and their data types (e.g. integer, date (if so which format), alphanumeric string, etc.). Most importantly, the data cannot be legally used by others without an attached license. I suggest attaching the Creative Commons Attribution-ShareAlike license, or follow the data publishing guidelines here: https://opendatacommons.org/guide/

5. (Materials and Methods lines 211-212 and 223-224) The authors state that verified photos and data from previous projects are available in the Smithsonian and eMammalWeb repositories. Please provide information enabling access to those datasets including their Digital Object Identifiers (DOI), links for access, and license information.

6. (Discussion line 298) The word “manpower” is sexist, please find a synonym or rephrase.

7. The inclusion of animal silhouettes made the figures much easier to understand. The authors thoughtfully included links to the websites from which the silhouettes were obtained, and I followed the links to spot-check a few of the images. Some of them are shared under the Creative Commons Attribution-ShareAlike (CC BY-SA) 4.0 license, which legally requires attribution to the author (not just a link to the website) and a statement of the license in the attribution. For example, the chipmunk image (http://www.supercoloring.com/silhouettes/chipmunk) lists Natasha Sinegina as the author. This check should be done for all third-party material used and to ensure their licenses are legally compatible with the PeerJ Creative Commons Attribution (CC BY) 4.0 license (https://peerj.com/about/FAQ/#license).
Experimental design: The authors used two examples of citizen science wildlife monitoring with camera traps. They were well chosen for the temporal contrast between a short-term, “one-off”, project verses a longer term study, and also contrast in habitat (forest verses savannah-like). This way, results from these studies can better illustrate the breadth of applicability for the authors approach.

I believe the study – from site description, organisation of volunteers, education and outreach, to analysis – was well designed and described with a good amount of detail. For example, important information such as the number of photos per trigger, frame rate, and threshold for re-triggering of camera traps are presented. These important details are surprisingly and unfortunately often unreported in other papers.

A few responses and minor suggestions:

8. (Materials and Methods lines 198-200) To whom were the Twitter control surveys sent? Were they residents in the same area? Were the sample size and demographics comparable to that of the citizen scientists?

9. (Materials and Methods lines 207-209) The authors used eMammal to verify volunteer animal identifications. I am curious if the authors had to verify the classification of every single image or was it a spot check on a subset? What was the amount of photos needing verification and how substantial of an effort was this? If significant expert verification effort was required, it may be worth a bit of discussion as this may have implications for others seeking to conduct similar projects. In addition, the authors should link to the online repository for the full eMammal source code and associated license to ensure verifiability and reproducibility.

10. Following the previous point, is there any information on the natural history expertise (or any other pertinent demographics) of volunteers when they signed on to the project? Knowing whether skilled/knowledgable volunteers are needed may be useful for practitioners in the future.

11. (Materials and Methods lines 219-221) I note that the main statistical analysis reported in this paper is the Pearson’s correlation for seasonal correlations. As far as I can tell no other statistical methods were used for the other comparisons. I believe the current methods and results provide sufficient support for the authors’ conclusions, but I am curious if other statistical methods have been attempted or considered?

12. (Materials and Methods lines 219-221) The authors used the proprietary statistical software JMP. However, there were no supporting files attached with the submission and I was not able to review the analysis. It would be better if the relevant files (e.g. JMP project or analysis files) for the analysis are published with this paper under an open source license (https://opensource.org/licenses) such as as the GNU GPLv3 or later (https://opensource.org/licenses/GPL-3.0).

13. (Materials and Methods lines 223-224) I couldn't understand the last sentence in this section e.g. “with the except two at Prairie Ridge”. Can the meaning of this sentence be clarified?

14. (Results line 234) “Sandburg Home… had significantly lower bear activity compared to nearby Thurmond Chatham.” This is reasonably clear in Figure 3, but from which statistical method was this significant difference obtained?

15. While it can no longer be done now, I note that it would be ideal to conduct surveys and interviews on participants before the start of a project like this. This will establish a baseline on which possible changes in knowledge, attitude, and behaviour can be discovered.
Validity of the findings: The results and discussion are clearly linked to, and robustly derived from, the research questions in the introduction.

16. (Results lines 260-263) It is noteworthy that participants were empowered to initiate their own outreach, e.g. authoring “educational materials in the form of homeowner association newsletters...”. To me this stands out from other engagement outcomes where participants simply gained knowledge and/or skills. I believe it is worth emphasising in the discussion the potential of citizen science to empower participants in becoming more proactive citizens.
Additional comments: The needs for, and challenges facing, large scale ecological monitoring are great. While it is not the first time that citizen science camera trapping has been proposed to address this, the authors have conducted an important and comprehensive study on how such a project may be realised. This accessible paper is a solid and useful contribution to the discourse not just for ecologists, but for citizen scientists and conservation professionals (e.g. reserve managers or policy makers) as well. A few minor edits would further enhance its value.

Thank you for the chance for provide this review.


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

Input:
Title: THE VALUE OF CITIZEN SCIENCE FOR ECOLOGICAL MONITORING OF MAMMALS
Review round: 1
Reviewer: 3

Output:
Basic reporting: See general comments below.
Experimental design: See general comments below.
Validity of the findings: See general comments below.
Additional comments: (lines 80-82) Within the introduction, I’d like for the authors to note the type of citizen science methodology they are using (co-created, etc) and show familiarity with the different project types so as not to cast one view of what Citizen Science is.

(lines 83-84) Management of a large amount of data is not a new problem-- perhaps the authors could point to examples outside of ecology where big data is being successfully incorporated into decision-making processes (transit, urban design, etc. are good places to look).

(lines 87-88) I would like more information on the “expert review” function and how this supports verification of these large datasets on eMammal.

(lines 93-94) Again, I would like the authors to spend more time on a discussion of the types of citizen science they are undertaking. One case seems quite top-down while the other appear to answer questions from a community in close proximity to the site where they are working.

(Between lines 101-108) There are two very different types of projects being proposed-- one in which management practices will be implemented by the community and one in which they are implemented by the Center. It would be interesting if the authors could dig further into the differences of these approaches. Going more in depth on the citizen science aspect and the different methods and approaches is compelling, but not pulled out enough in this paper.

(lines 148-149) The article could use further explanation on why the cameras were left unchecked and (line 149) the reason for random site selection (perhaps moving lines 218-219 up or saying this earlier as well).

(line 197-200) Why not the same surveying approach to the Sandberg Homes group? If not surveying, what did the authors use to evaluate the approach with the Sandberg Homes group?

Beginning on line 253, because this is a relatively compelling use of citizen science to support community questions, I’d offer that the researchers should reconsider the use of terms such as “volunteers” and “participants”. These terms relegate people working on citizen science projects to being in service to the researchers, rather than empowered as co-researchers who are asking questions about their community and environment and also using the data to do things such as outreach to media and sharing their findings to neighbors via newsletters such as in the Sandberg Homes case. Although this is many times not valued as highly in citizen science, activities like this net highly relevant outcomes and should have higher placed value.

Line 265 notes there are 531 volunteers, but line 267 says only 9 completed the survey. Either this is written in a way that isn’t clear or more explanation needs to be given for the low survey numbers.

(lines 292-294) There is an argument to be had for citizen scientists driving down the cost of doing science, but by putting this in the forefront of the discussion section, potentially interesting information gained about educational and behavioral changes noted just above in the previous section is buried. Perhaps move the section that begins on line 318 up to meet the rest of the citizen science discussion. The chop in citizen science use analysis because of the discussion of what you discovered from an ecological perspective during the monitoring doesn’t quite flow.

The two sentences on lines 334-337 are incredibly compelling-- your work and approach is supporting people in creating their own planning efforts. This finding is buried and not built out, it would be great to see more focus on how and why this type of deep engagement in working towards community goals was successful in your example.

Lines 343-347, there is a lot of writing that is being done on this, especially from the citizen science and open technology fields. The assumptions and statements the authors make are accurate, but could be backed up with literature.

Charts and figures are clear-- would the authors consider including an image from the camera traps to demonstrate the raw data being used in this project or visual workflow of what citizen scientists are walking through when using eMammal?


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

Input:
Title: THE IMPORTANCE OF SPONGES AND MANGROVES IN SUPPORTING FISH COMMUNITIES ON DEGRADED CORAL REEFS IN CARIBBEAN PANAMA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article meets the standards listed for this section (Basic Reporting) in that is is mostly clearly written. My concerns with the article are more general, and have to do with the overall approach to the topic. See notes below under General Comments.
Experimental design: I disagree with the analytical approach, and thus the nature of the research question. Since my concerns deal with the structure of the authors' approach, their experimental design, as well as their conclusions, I summarize my concerns under General Comments.
Validity of the findings: Since I don't agree with the overall approach of the authors, I don't feel than their findings are valid in the broader context that I think they need to address. Within the smaller scale context of their approach, their findings are valid.
Additional comments: I think that the authors have the makings of a very good manuscript. They have sufficient data from a broad geographic range. However, I do not think that the manuscript in current form is acceptable. My concerns are with the overall structure of their arguments, as outlined below.
General Comments:
I do not believe that general diversity indices are good proxies for estimating ecological function. For example, one can measures the same diversity for a system that is comprised of entirely different species. This can affect competition, predation, etc.  The authors address this to some extent by calculating their community metrics to account for trophic level as well as disproportionately abundant species. Yet, they don’t account for the likelihood that their smaller size classes are mixtures of small-bodied fishes (which are likely residents) and juveniles (which are likely temporary). Each of these groups has different functions, will be affected differently by habitat degradation or change, not to mention the overall connectivity of the habitat mosaic. To the latter point, I suggest that small-bodied resident fishes are less likely to be affected by fragmentation (a good measure of habitat degradation) than species that ontogenetically shift among habitats. See as an example: Dahlgren, C., G.T. Kellison, A.J. Adams, B.M. Gillanders, M.S. Kendall, C.A. Layman, J.A. Ley, I. Nagelkerken, J.E. Serafy. 2006. Marine nurseries and effective juvenile habitats: concepts and applications.  Marine Ecology Progress Series. 312:291-295.
A relatively diverse species assemblage that depend on different habitats than corals doesn’t necessarily translate to ecological resilience. In fact, I suggest it is more likely a phase shift, especially since different invertebrates are providing structure. If so, the discussion should be more about whether the phase shift is to a more or less complex species assemblage as well as whether it includes a trophic (or other) shift. I suggest the authors read White and Jentsch, 2001. The Search for Generality in Studies of Disturbance and Ecosystem Dynamics. Progress in Botany, Vol. 62. This article provides a good structure for examining disturbance (which is, in essence, what the authors are doing).
On a similar note, the White and Jentsch article should be helpful framing the anthropogenic disturbances that the authors are studying. In short anthropogenic disturbances differ from natural disturbances in the disturbances themselves  as well as the ecological impacts from these disturbances. For example, “Does this southwestern Caribbean fish community show signals of reef degradation and over-fishing?” mixes different types of anthropogenic disturbances (direct, indirect, long-term (chronic), pulse) that one might expect to have different impacts.
How do these disturbances differ from natural disturbances (e.g., hurricanes)? Are fish communities more or less resilient or resistant to these vs natural disturbances? Would provide some overall ecological context. Might also speak to the ability of these ‘new’ systems to respond to natural disturbances.
Specific Comments:
Line 87 – “killed up to 95% of the hard coral cover” Where? In Panama, at the study site, worldwide?
Line 89 – “The persistence of invertebrate communities on these degraded reefs suggests that some resilience mechanisms are operating”.  Define “resilience”. Differentiate resilience, resistance, phase shift, as in White and Jentsch 2001. I suggest that the authors consider this a phase shift since it is different invertebrate species that are now the main structure providing organisms, and that the overall fish assemblage differs from what one might call “natural”. In addition, given these differences in invertebrate communities and fish species assemblages, I would expect that this new phase will have a different level of resistance or resilience to continued anthropogenic disturbances and natural disturbances (hurricanes).
Methods
Some of my comments below may be in error due to the fact that it was unclear to me the extent that reefs, seagrass, and mangrove habitats were visually surveyed at all of the study sites (BDT as well as the Caribbean sites that are listed). Were only reef surveys conducted at the Caribbean sites, or also seagrass and mangroves?
Line 124 – were the site types paired by location (e.g., multiple Florida sites, multiple Southern Caribbean sites) or pooled across all surveys? In other words, did the authors control for potential location bias whereby differences may have been partly due to location-specific ecology? This appears more apparent in Figure 2, but is still never explained in Methods, and not really broken down in Results.
Line 130 – why were seagrass and mangroves only surveyed at BDT? Why not at other locations? How do we know whether the findings at BDT are different/same compared to other locations with or without protections (e.g., NTZ)?
Line 141 – “abundance within size classes (10 cm size bin and below; 12.5-20 cm size bins; 25 cm size bin and above)”.  This makes it difficult to differentiate small bodied species from species that use seagrass/mangroves as juveniles only (e.g., Haemulidae, some Scaridae, Lutjanidae, Serranidae). Thus, it’s difficult to discern whether the non-reef habitats continue to function as juvenile habitats (even though adult habitats are degraded on the reef to the extent that juveniles may not successfully transition to adults, or at least not survive) or if these communities are mostly small-bodied resident species. This is important when considering whether this is the same community that is resilient, or if a phase shift has occurred.
Line 235 – 243 – To what extent are these results due to differences in species composition of mangrove habitats rather than anything to do with reef habitat degradation and overfishing? Perhaps surveys at other reef sites should have also included mangrove-associated habitats. Cite the article showing relationship of mangrove proximity to coral reefs and fish species composition.
Similarly, as depicted in Figure 2 – Shouldn’t the other Caribbean sites (non-BDT sites) also be examined by distance from mangroves? Since this was such a significant factor in this study, and the error bars are so large in Figure 2, if different habitats were sampled this may bias results. In addition, as the authors note (e.g., Mumby et al 2004), distance from mangroves to reef can influence species composition on the reef (due largely to the nursery value of mangroves to some species).
Line 247 – re San Andres Archipelago – was there a single site here, or multiple sites? Were similar surveys conducted in other ecoregions?
Lines 275-282 (which appear to link species composition to lack of high relief coral reef habitat) and Lines 299-303 (which now blame species composition on overfishing). Coral habitat degradation and overfishing can both causes changes in species composition and fish abundance, but the effects of each type of disturbance can differ, or if they co-occur can act synergistically. Again, see White and Jentsch for a general discussion.
Line 305-308 – what are possible causes and effects of low herbivorous species abundance? The Florida Keys reef tract has high Scaridae and Acanthuridae abundance, yet has low live coral cover and high algae cover on reefs.
Line 319-329 – this should be the sole focus of the paper. They observed different species composition due to decline in live coral cover and loss of habitat complexity. Whether to do with overfishing or other disturbances – these are potential explanatory variables there is no cause established here.
Line 334 – “Our study suggests that the positive effect of mangroves as nursery and feeding grounds can overcome and compensate some aspects of reef degradation in an ecosystem that has suffered multiple stressors.”
I’m not entirely sure of the intended meaning of this sentence. If mangroves serve as nursery grounds for species associated with the reef as adults, how does this compensate or overcome reef degradation? There is still no adult reef habitat, so ontogenetic habitat shifts can’t be completed. In other words, the juveniles that are abundant in mangrove habitat don’t represent a reproductive population that contributes to future generations if they are not able to find adult habitat which allows them to survive and reproduce (or they are harvested before they can reproduce).
Line 336 – “There are, however, non-linearities in mangrove influences on reefs, with negative influences at distances below 100 m. The reef-mangrove distance driving the highest abundance of carnivores was identified to be between 100 and 250 m.”
I am intrigued by this statement. I think that additional explanation is needed. I am not aware of studies that have documented this specific of a relationship (especially the negative influence). Mumby et al (2004) found a relationship between species composition on reefs and proximity to mangroves, but in more general terms, and not a negative relationship. Further, what is meant by “influences”, whether positive or negative? Are differences in species composition positive or negative, or merely a reflection of the habitat mosaic that supports (or doesn’t) the ontogenetic habitat requirements of different species? If the data truly show this as a result, this would, in itself, be a valuable manuscript.
Figure 2, A – are the error bars SD or SE?
Table 2 – I don’t think it’s valid to present the data at the level of species because the ontogenetic habitat requirements differ among species within the same family. For example, juvenile acanthurids of the three species observed in this study all use different habitats as juveniles (on-reef and off-reef, depending on species). So combining these species in a single factor for analysis introduces bias. See, for example:
Robertson, D. R. 1988. Abundances of surgeonfi shes on patch-reefs in Caribbean Panama: due to
settlement, or post-settlement events? Mar. Biol. 97: 495–501.
Shulman, M. J. 1985. Recruitment of coral reef fishes: effects of distribution of predators and
shelter. Ecology 66: 1056–1066.
Shulman, M.J. and J. C. Ogden. 1987. What controls tropical reef fish populations: recruitment
or benthic mortality? An example in the Caribbean reef fish Haemulon flavolineatum. Mar.
Ecol. Prog. Ser. 39: 233–242.
Shulman et al. 1983. Priority effects in the recruitment of juvenile coral reef fishes. Ecology 64: 1508–1513.
Adams, A.J. and J.P. Ebersole. 2004.  Processes influencing recruitment inferred from distributions of coral reef fishes. Bulletin of Marine Science. 75(2):153-174.
Adams, A.J. and J.P. Ebersole. 2002. Use of back-reef and lagoon habitats by coral reef fishes.  Marine Ecology Progress Series. 228:213-226.


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

Input:
Title: THE IMPORTANCE OF SPONGES AND MANGROVES IN SUPPORTING FISH COMMUNITIES ON DEGRADED CORAL REEFS IN CARIBBEAN PANAMA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors aimed to understand the factors driving the communities of fishes observed on coral reefs in Bocas del Toro and other Caribbean locations.  They used a fish community assessment method designed by two of them and a large suite of environmental and biological parameters. The general approach was to look for correlations between the parameters and the fish community measurements.

I have annotated the manuscript throughout, so provide only a general synopsis below:

The manuscript is fairly well written and organized, but there quite a few places where corrections or edits are required. However, the methods and discussion fall short.  Some of the comparisons that were made are difficult to assess with the given information (e.g., why would open sand in seagrass be important? This and other metrics are not mentioned in the methods) and the exact methods used to gather the information insufficient.  The discussion is not terribly well organized and does not interpret some of the comparisons that were made.  In some instances, broad and substantial statements are made without much discussion, or support from the results.
Experimental design: The design was not completely clear as it was not always obvious what was being measured and where. Were all metrics measured at ALL sites (reefs, seagrass, and mangroves)? Not all metrics were relevant for all sites. Many other comments are made within the manuscript.
Validity of the findings: This is really the crux of the problem with the manuscript.  It is basically a study of correlations and correlations do not provide cause and effect.  In too many instances the authors make assumptions about the cause of the correlations they found. In other instances, the correlations are simply correlations that do not entirely make sense and are not explained (e.g., why would proximity to mangroves drive abundance of carnivores?). See other comments within the manuscript.
Additional comments: Clearly, an enormous amount of effort went into collecting the data for this study and there is value in it.  I suggest that the authors refocus their analysis on specific comparisons that makes sense and keep their interpretation to those results. I would suggest that they focus more explicitly on the fishing restriction schemes and the proximity to mangroves and seagrass beds as the parameters. The structure provided by sponges is also an interesting and compelling parameter, but describe what was measured more explicitly. If they wish to include other parameters, they should make sure they explain the reason for including them, the methods for gathering the information, and the relationship that might be expected.

Regarding interpretation, the arguments for the cause of these patterns need to be more carefully presented so they do not extend beyond the results.  When speculative, this should be noted and alternative explanations should be presented.


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

Input:
Title: THE IMPORTANCE OF SPONGES AND MANGROVES IN SUPPORTING FISH COMMUNITIES ON DEGRADED CORAL REEFS IN CARIBBEAN PANAMA
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: The Methods are now better described, and analyses and have been adjusted to the revised approach.
Validity of the findings: The findings and conclusions are now in line with the data.
Additional comments: The authors have done a good job of addressing my comments. I think that the discussion has been stepped back to more appropriately address their results, and that the study is appropriately placed in a broader context.

There are a number of editing items that need to be addressed (misplaced words, typos). Some are addressed below, most are not. Most of my specific comments reference these editing needs. Two of my specific comments, however, I think should be addressed as part of a minor revision.

Line 13 – 14: “habitat degradation” is used as both the effect and the cause in this sentence.
Line 12: I don’t understand how the Cayman Islands can be considered part of the Bahamian ecoregion. Perhaps similar reef topography, but certainly not in the same region. And the extent of mangroves in the Turks and Caicos is much higher than the Cayman Islands. What is the justification for this?
Line 190: ‘respectively’ is misplaced here
Line 208: Regarding :”worldwide” - Wouldn’t this be true for a comparison of Caribbean and Indo-Pacific reefs, the I-P being so much more diverse in general? I suggest sticking to Caribbean comparisons. Suggest removing, as the argument can be made without it.
Lines 210 – 211: What about comparison to other OZs not in BDT, in addition to the MPAs and NTZs? Isn’t this an important part of the comparison? Are the BDT sites the same as, worse than, better than the other OZs? This is shown in the figure, but needs to be referenced in the text. Why is the BDT area worse than other OZs in the Caribbean? Is this entirely due to fishing or are other factors at BDT worse than in other locations in the Caribbean.
Line 291:  “resilience” delete
Line 342: Please explain how the small size of S. iserti allows it to escape environmental pressures. I can see that its small size means it is not targeted by fishing, so it is not harvested. But what other anthropogenic pressures does it escape because of its size? Perhaps this sentence should be revised to specifically state that its small size allows it to escape pressure from fishing.


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

Input:
Title: THE IMPORTANCE OF SPONGES AND MANGROVES IN SUPPORTING FISH COMMUNITIES ON DEGRADED CORAL REEFS IN CARIBBEAN PANAMA
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors have correct many of the problems with the writing of the manuscript, but it still suffers from a high number of grammatical errors and ambiguous wording. I have fixed many of the grammatical issues in the edited version attached. Other comments are embedded.

The methods are more clearly described, but there should be at least a brief description of the RLS method 1 protocol.

The figures are fairly well constructed, especially the map of sites, but figures 4 and 5 are not even referenced until the discussion.  Figure 5 is not intuitive.  There must be a better way to convey this information.

The water quality sampling is still included in the methods, although it is not in the results or discussion.
Experimental design: The experimental design is much clearer in this revised version and the goal of the research is apparent. In most cases there are details on how the data was collected an used, and where there were shortcomings.
Validity of the findings: The authors did a much better job of focusing their analysis and interpretation on relationships that made sense, instead of casting a wide net to see where it landed, as they had done prior.  However, there are still questions about their interpretations and places where I think they have made assumptions or drawn conclusions not supported by the data. For example, the assumption that mangroves serve as nursery grounds for all these fish species is just an assumption. It could very well just be an alternative habitat for many.  These instances are all pointed out explicitly in the edited version of the manuscript attached.
Additional comments: The manuscript is much improved, particularly with regards to the focus.  However, there are still quite a few fundamental problems that need to be addressed.  However, I do not think these are insurmountable.


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: LIMB-USE BY FORAGING MARINE TURTLES, AN EVOLUTIONARY PERSPECTIVE
Review round: 1
Reviewer: 1

Output:
Basic reporting: The text is clear and professionally put together. Literature is well reviewed and supports the manuscript arguments.
Experimental design: The research question is well defined and appropriate to the journal.
Validity of the findings: I believe the authors are a bit more speculative than needed at times, but this does not detract from a good read. The arguments are well presented and researched, and the conclusions are valid (although I suggest they acknowledge the other mechanisms through which these evolutionary processes may have occurred. See my detailed notes to the authors below.
Additional comments: This is a nice interesting read, and I think it would be interesting to others also. I think at times the authors read a bit too much into the findings, which could similarly have been written up by someone else as co-evolution processes – something along the lines of “imagine what a flipper might look like if there was no need to swipe or hold or dig or corral?” I am simply saying that while the authors argue that these are cases of exaptation, they could just as easily be of co-evolution. Given this, I think it would be easier to simply stick to what is known and only make some suggestions as to how old this might date back, and acknowledge the other pathways of how this process may have come to be.

I also think the authors made a big mistake in not reaching out to the sea turtle community for additional material for this thesis. Not everyone posts their video and imagery to the internet (I am one of those) and thus a very wide range or actions stands to have been lost. This does not mean the paper would not already have captured much of what has been seen, but it does point out a limitation in sampling.

Overall I think there are a few places where the MS could be tightened up, made more focused and less-speculative, but I also think this is a useful short addition to the body of knowledge on sea turtles in the public domain.

Some specific comments are made below:

Line 16: I am not so sure the word unexpected is correct here. There is no reason why an animal would not adapt if it could. So it is not so much that it is unexpected but rather uncommon or uncommonly documented.

Line 48 citation should be the first e.g. 2017a

Line 97 Word should be studies

Line 97 Might be best to clarify that this is in the mechanics of foraging rather than foraging in general – of which there have been many studies.

Sentence at lines 98-100 belongs in the Introduction and not in the Results section.

Line 102 If this has not been studied much, it might not be that it was not previously believed, It might just be something that previously received little attention – maybe because in today’s climate of endangered species there other issues are considered a higher priority to study and understand.

Line 103. There is no previously described foraging by green turtles described. It is not even mentioned above. The reader would need to know someone studied this, no?

Line 105 and elsewhere – the use of the word corralling is typically for something that moves – we corral bulls and horses. We do not corral non-motile sponges. Might this be better as collect, amass, round up, bunch up, or secure?

Similarly, the word capture is somewhat misleading as none of these are trying to escape. I suggest finding a better word here also.

Lines 107-108. How can the authors be certain these strategies are not necessary? On some reefs the organisms that the turtles seek are more cryptic than on other reefs, and turtles may be ‘forced’ to become adaptive. I am not at all certain this statement can be made with any validity.

Lines 109-117 could use a lot more explanation to make this more understandable to a public less-informed of these behaviours. Lobtail feeding… kerplunking… these could all use a short explanation. Understood that these show up In the table, but it would be worth some short inclusions of the less common ones in the text.

Lines 138-141 Here the authors correctly use the word ‘if’ because it is unknown if this is the case. But the Abstract reads as if this is conclusive. I suggest the Abstract be reworded to suggest only that this might be possible.

I am unsure of the meaning of lines 149-149. Given the huge disparity in animal forms, would this not be expected? What is being suggested there that is new and novel?

Lines 154-159 I believe the discussion really should be centered around exaptations in sea turtles and not delve into the why’s of dolphin and whale design. I do not see how this supports the discussion.

Lines 169-171 It is not possible to determine turtle sex simply by looking at the tail. These could easily have been immature, sub-adult males. I suggest the authors refrain from assumptions. It might be best to use the word putative here to indicate this is assumed but not known for certain.

Line 173 See my earlier comment on the use of the word unexpected.


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: LIMB-USE BY FORAGING MARINE TURTLES, AN EVOLUTIONARY PERSPECTIVE
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall, this paper is clearly written and I think the main point of the paper, that the use of forelimbs in foraging by marine turtles may have evolutionary relevance, is probably valid. Unfortunately, the evolutionary perspective needs to be much better demonstrated and the authors’ declaration that their article represents the first observation of forelimb assisted foraging in adult marine turtles is not valid. Forelimb use during foraging by mature sea turtles is a well-documented behavior and has been described in the scientific literature as early as the mid-1990’s.

Ex:

Limpus C., Couper P., & Read M. 1994. “The loggerhead turtle, Caretta caretta, in Queensland: population structure in a warm temperature feeding area”, Memoirs of the Queensland Museum, 37:195.

Houghton J., Woolmer A., & Hays G. 2000. “Sea turtle diving a foraging behavior around the Greek Island of Kefalonia”, Journal of the Marine Biological Association of the United Kingdom, 80:761-762.

Schofield G., Katselidis K., Dimopoulos P., Pantis J., Hays G. 2006 “Behaviour analysis of the loggerhead sea turtle Caretta caretta from direct in-water observation”, Endangered Species Research, 2:71–79.

In fact, forelimb assisted foraging in adult loggerhead turtles is so well known that it has been termed “infaunal mining” (See - Preen A.R. 1996. Infaunal mining: a novel foraging method of loggerhead turtles. Journal of Herpetology, 30, 94–96.) The authors should consider focusing the discussion of their paper on the unique foraging behaviors documented in their study (corralling, leveraging, holding, and swiping) or at least rephrasing/deleting the statements in the manuscript which imply the novelty of their observations.
Experimental design: Lines 67-68 – “We documented marine turtle foraging behavior from underwater surveys, web image and video searches (e.g., Google, YouTube, Vimeo, Flickr, Shutterstock)...”

Do the authors provide a list of these images and videos? Have the videos or images been uploaded to an online repository? Any visual data incorporated into the study should be accessible to other researchers and many of the URL’s for YouTube and Vimeo videos are not permanent and could expire/change at any time. The authors should consider contacting the parties responsible for producing any of the visual data used in the study and gaining permission to deposit the videos/images into a publicly accessible digital repository.

Line 92 – “Evolutionary relationships and divergence times are from Timetree.org”

Timetree.org should not be considered a primary source of information regarding the divergence estimates of sea turtles as the dates on Timetree.org are not based on the currently accepted best practices for such estimates. Recommended sources include:

Parham J., Donoghue P., Bell C. et al. (22 co-authors). 2012. “Best practices for using paleontological data for molecular divergence dating analyses.” Systematic Biology, 61:346–359.

Joyce W., Parham J., Lyson T., Warnock R. & Donoghue P. 2013. “A divergence dating analysis of turtles using fossil calibrations: an example of best practices.” Journal of Paleontology, 87, 612–634.
Validity of the findings: The authors do a good job of summarizing the different methods of foraging observed in extant chelonioid species, however, I think in order to say much about the presence of such behaviors in extinct species at the base of the chelonioid lineage, the authors needs to summarize quite a bit more data and I worry that this may be beyond the scope of the study but this is for the authors to decide. For example:

Lines 132-133 – “...it is currently unknown if there are any detectible physical predictors of limb-use that could be used for studying the origin of this behavior.”

Have the authors considered examining the anatomy of sea turtle forelimbs and those of other marine tetrapods known to engage in similar behaviors to see if there are any physical predictors associated with this type of limb usage? Vertebrate functional morphology and biomechanical inferences from comparative anatomy have been implemented across a multitude of extinct and extant species to assist in the determination of limb usage. Though foraging behavior would most likely be considered a biological role of a structure rather than its function, with the former being significantly more difficult to assess using traditional comparative anatomy, this may be an area the authors could investigate to further support their argument that no such physical predictor exists.

Line 137 – “...the limbs of these species are not as specialized as marine turtle foreflippers.”

This line of discussion is somewhat confusing as there is no discussion or citation provided regarding the morphology of aquatic, terrestrial, and marine turtle forelimbs as it pertains to the degree of specialization to individual ecologies. One potential source of such information may be:

Joyce W. and Gauthier, 2004. “Paleoecology of Triassic Stem Turtles Sheds New Light on Turtle Origins”, Proceedings of the Royal Society of London, Vol. 271, No. 1534.

Additional information on turtle forelimb morphology framed within an historical and ecological context can be found in:

Joyce W. 2007. “Phylogenetic Relationships of Mesozoic Turtles”, Bulletin of the Peabody Museum of Natural History, Vol. 48, p. 51.

Lines 137-138 – “This does, however, support the suggestion that this behavior was present in an ancestral turtle.”

This seems quite speculative as any discussion of paleoecology would need to rely heavily upon comparisons between the anatomy of fossil and extant taxa. While I agree that the presence of forelimb assisted foraging strategies in terrestrial, semi-aquatic, and marine turtles may serve as an indicator that these behaviors may have existed in some form in an ancestral turtle, this point should be better supported by data. Whether these data are purely anatomical in nature or a combination of ecological inferences based on an analysis of comparative morphology is up to the authors to determine. If the authors decide that a detailed anatomical discussion of turtle forelimbs is beyond the scope of the study, then perhaps these statements could be rephrased to better reflect what is currently known regarding the correlation between forelimb anatomy, biomechanics, and feeding ecologies in turtles (See Joyce and Gauthier, 2004).

Lines 138-139 – “If this behavior was present when marine turtles evolved, approximately 120 million years ago...”

This statement should be drawn from empirical data (see previous comments) rather than simple inference. The authors should also consider citing additional source regarding the earliest marine turtles (Ex. - Cadena E. and Parham J., 2015. Oldest known marine turtle? A new protostegid from the Lower Cretaceous of Colombia. PaleoBios, 32, 1-42)
Additional comments: Abstract

Lines 17-18 – “Here, we add marine turtles to the diversity of marine tetrapods known to use limbs for foraging...” Limb assisted foraging in marine turtles is well-documented. (See previous comments)

Introduction

Line 27 – “(Chelonioidea Oppel, 1811)” should be inserted following “Marine turtles”.

Lines 41-43 – Could the sentence regarding the presence of rudimentary limb-use for foraging be combined with the following sentence to better illustrate the connection between the two statements?  Ex. “Rudimentary limb-use for foraging is observed in a range of terrestrial and aquatic taxa therefore, this behavior likely evolved in ancestral tetrapods...” This is only a suggestion assuming that I am correctly inferring that the authors are implying an evolutionary relationship between the terrestrial/aquatic and marine lineages.

Line 52 – “(Cheloniidae)” should be deleted. Cheloniidae refers only to hard-shelled sea turtles and excludes Dermochelyids (Dermochelys coriacea).

Lines 55-56 – “To date, however, marine turtle foraging mechanisms have received little attention.” This is not accurate. (See previous comments)