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: BIOGEOGRAPHY RATHER THAN SUBSTRATE TYPE DETERMINES BACTERIAL COLONIZATION DYNAMICS OF MARINE PLASTICS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The language was good and reporting style clear and easy to follow. Overall, the structure, referencing, and background provided were professionally done with only very minor language mistakes. Raw data, however, is largely missing from the supplement. These include: ASV and taxonomy tables, and pairwise distance matrices used for statistical tests. Additionally, for replicability and transparency, all sequences generated within this study must be deposited in an archive and made accessible to the public, which was not indicated here.
Experimental design: The primary aim of the study is an interesting one, and preliminarily addresses differences in microplastic-associated bacterial communities on a more global scale and the factors that shape them. Understandably, conducted as a part of a student training program, there exist quite a few gaps - most notable of which is the lack of recorded environmental data. This, however, is exacerbated by a further lack of more in-depth descriptions of the incubation experiment in itself. Method of deployment and, perhaps more importantly, description of the conditions at the incubation sites are missing completely. What are the influencing water bodies and how are the hydronamic patterns at these sites? These would all greatly supplement the report overall but also the discussion, where inferences made are weakened by the lack of measured environmental data. With the inclusion of some environment descriptions, more meaningful inferences can be made of the data obtained in this study.
Validity of the findings: The results provided are clear and necessarily replicated. Conclusions made, well-linked to the primary aims of the study, were reasonable and provided the right amount of speculation without overstretching assumptions.
Additional comments: 1.	Line 39 – 40: ‘…estimated that 3 % of annual plastic production enters the ocean each year…’ should be ‘estimated that 3 % of plastic produced annually enter the ocean each year…’

2.	Line 52: ‘…describe the microbial life inhabiting marine plastic debris…’. The word ‘inhabit’ by definition means to live in which is not quite the case here. Perhaps a more precise word such as colonize or attached to?

3.	Line 54: ‘…into contact with an environment’ should be ‘…into contact with the environment’.

4.	Line 69: ‘…duration of biofilm growth’ might more accurately be replaced with ‘age of biofilm’.

5.	Line 85: ‘naturally occurring’ should be ‘naturally-occurring’.

6.	Line 109: ‘…was melted onto one side of individual glass microscope slides’ should be ‘were individually melted onto one side of glass microscope slides’.

7.	Lines 105 – 110: Manufacturer’s information provided for the different polymer types are incomplete – disclosed with some are the company name and location while for others this information is missing.

8.	Lines 110 – 113: How were the glass slides deployed? What were they attached to? A brief description of the incubation design might prove helpful here. Additionally, please provide some description of the conditions at the incubation sites. If one of the objectives of the paper is to investigate the role of environmental conditions in shaping biofilm community composition, more information on the characteristics that mark the studied environments are crucial here.

9.	Lines 113 – 114: Perhaps this ‘RNA-later-type solution’, if not the actual brand name for a purchased solution but self-prepared, should better be referred to as a stabilization solution or buffer.

10.	Line 119: No comma after ‘approved by’.

11.	Line 123: Semicolon missing between ‘Japan’ and ‘and’.

12.	Line 128: ‘…the surface-scraped biological material…’ should be ‘the biological material scraped off the surface of each slide…’ as the language used here implies that the surface of the biological material was scraped, not that of the slides.

13.	Line 144: Open bracket missing before ‘5’-’.

14.	Line 150: Please include link to archive where the sequences in this study have been deposited (e.g. Sequence Read Archive (SRA) accession number).

15.	Lines 163 – 164: What parameters were used for classify-sklearn? Also, which parameters were used to train the classifier?

16.	Line 165: Unassigned sequences on which taxonomic level?

17.	Line 167: ‘…was rarefied to 8000 sequences…’ I think a brief justification (like the one from line 225 on subsampling based on lowest read count) should also be included here.

18.	Lines 174 – 176: I believe the ‘RCore Team, 2019’ citation should be referenced following mention of the stats package as it is a R-core package while the analyses were performed in RStudio which should be mentioned and also cited differently (i.e. RStudio Team (2020). RStudio: Integrated Development for R. RStudio, PBC, Boston, MA URL http://www.rstudio.com/)

19.	Line 178: ‘free, open-source…’ is redundant. Open-source in itself means that the software is freely available.

20.	Lines 180 – 181: I am not sure it is correct to refer to Faith’s diversity index as a measure of phylogenetic relatedness. It is correct that the calculation of Faith’s PD is based on the phylogeny of the community but it measures the diversity/richness. Faith’s PD = the sum of the branch lengths that span the tree, hence the greater the sum of the branch lengths, the greater the number of branches. One cannot, however, infer the relatedness of individuals solely based on this metric. For example, a high PD value could stem from a highly branched clade of closely related individuals or from greater separation closer to the root of the tree.

21.	Line 183: Not sure there is such a thing as ‘ASV-level alpha diversity’. The violin plots serve to visualize the distribution of observations (among the different samples of each polymer type). ASVs are proxies for species, so what is ASV-level alpha diversity?

22.	Lines 184 – 186: Why were the controls included in the experimental design just to be removed from the comparison within the analysis? It is unclear here from which analyses exactly the controls were excluded seeing as how, based on the figures/tables provided, they were included in the alpha diversity calculations, ordinations, and selected multivariate analyses.

23.	Line 189: Would be better to mention the significance level as α = 0.05. Same goes for line 201.

24.	Line 188 and line 191: The use of the word ‘sample types’ implies or could be understood as a comparison just between the different substrate types. Perhaps better to just refer to it as ‘samples’ here which would then encompass the different incubation sites and substrate types.

25.	Line 193: ‘…assistance of the phyloseq R package’ should be ‘assistance of the R package phyloseq’.

26.	Lines 195 – 203: What was the motivation to calculate phylogenetic distances based only on unweighted metrics and not weighted? Also, ‘UniFraq’ should be ‘UniFrac’.

27.	Lines 201 – 203: PERMANOVA usually needs to be accompanied by PERMDISP (Permutational Analysis of Multivariate Dispersions) which detects for large dispersions/variations within groups and more importantly ensures that significant PERMANOVA p-values are really the product of between-group differences and not within-group variation.

28.	Lines 205 – 206 (and again in line 207): What is ‘median relative community composition’?
Additionally, consider rephrasing this sentence as it is presented more as a result (particularly: ‘A bubble plot displayed phyla…’) rather than an action that was performed.

29.	Lines 208 – 210: ‘Family names’ and ‘order names’ may be better referred to as assignments (e.g. taxonomic assignments on the family and order levels). Also, a little confused by this sentence. Were the reads removed or just collapsed to the next highest classified taxonomic level?

30.	Lines 221 – 222: ‘…36 samples from four polymer types’ should be ’36 samples composed of/consisting of four polymer types’. Also, if there were 2 slides of each substrate type at each site but you ended up with 36 samples in total, what happened to the other 4 slides?

31.	Line 228: ‘…reads were distributed among 12361 unique features’ should be ‘reads were made up of 12361 unique features’.

32.	Line 231: Might be helpful to start here with a brief mention of the mean or range of values observed for the different diversity indices before getting into the comparisons. These are important to provided a clearer idea of the diversity of the communities found on the different substrates at each site.

33.	Line 234 – 235: For Pielou’s evenness ‘p < 0.001’ but for Faith’s PD ‘p = 0.003’? Why is one a range and the other not?

34.	Table 1B: ‘permutation’ should be ‘permutations’.

35.	Lines 263 – 264: Again, how does inclusion of the controls interfere with any of the analyses? Perhaps some confusion here but ‘removed from analysis’ encompasses all analyses. Was it the case that the control samples were excluded from ALL analyses, including statistical tests? This is important and if not the intended meaning, please consider rephrasing.

36.	Lines 300 – 303: ‘Communities on plastic-coated glass slides from all locations were similar in evenness, while the communities from the equator (Cape Verde) had a significantly higher evenness than the mid-latitude incubation locations (Chile, Japan, South Africa)’. This sentence contradicts itself as it is easily understood as ‘Communities from all locations were similar yet significantly different’. Does the first part of the sentence refer to a comparison between substrate types? If so, some rephrasing is required because that is not clear.

37.	Lines 333 – 336: How does the wide range of diversity values observed among control samples indicate that it is has a greater diversity than those of plastics? Does a wide distribution of data points not indicate only that there is, as stated by the authors, variation within the group?

38.	Lines 355 – 357: Seems a little contradictory that in the previous statement you mention that there is currently no clear consensus on whether bacteria exhibit substrate-specificity yet in this sentence it is ‘generally […] agreed’ that they do not. It then becomes quite convoluted in the following sentence, where authors attribute the lack of specificity observed in this study, to the age of the biofilm given especially that it was just mentioned that other studies have observed such specificity even after longer periods (i.e. 21 months: Kirstein et al. 2019).

39.	Lines 385 – 387: Were these families also detected in this study and associated with these polymer types or why is this being mentioned here?

40.	Line 390: Cellvibrionaceae is referred to here as ‘detected in our study but were not previously documented as members of bacterial Plastisphere communities’ but was already mentioned in line 383 to be reported by Oberbeckmann & Labrenz and Cheng et al..

41.	Lines 401 – 404: How did your findings align with those of Kesy et al. and Oberbeckmann et al.? Were Vibrio found more abundantly on the glass controls used in this study or is this claim made purely based on the fact that Vibrio made up a very small proportion of the overall community? Bear in mind that the latter means a very different thing from the former.


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: BIOGEOGRAPHY RATHER THAN SUBSTRATE TYPE DETERMINES BACTERIAL COLONIZATION DYNAMICS OF MARINE PLASTICS
Review round: 1
Reviewer: 3

Output:
Basic reporting: This was a clear and well-written paper that I enjoyed reviewing. The authors have provided a good overview of current plastisphere research, however, there are a handful of recent papers that do characterise the plastisphere in the Southern hemisphere that I think should be discussed/mentioned (there are also potentially others published during 2021, but I most recently searched the literature at the beginning of this year):
1.	Cornejo-D'Ottone et al. 2020 (16S rRNA gene sequenced – focus of the paper on greenhouse gas cycling, sampling in subtropical South Pacific gyre) https://doi.org/10.1016/j.chemosphere.2019.125709
2.	Lacerda et al. 2020 (focused on fungi not prokaryotes – sequenced ITS2 and 18S rRNA genes, Western South Atlantic and Antarctic) https://doi.org/10.1111/mec.15444
3.	Zaiko et al. 2016 (focused on eukaryotes – 18S rRNA gene sequenced, incubations in Lyttelton, New Zealand) https://doi.org/10.1080/08927014.2016.1186165
4.	Tobias-Hunefeldt et al. 2020 (16S and 18S rRNA genes sequenced, incubations in Otago, New Zealand) https://doi.org/10.1038/s41396-020-00833-6
5.	Lee et al. 2016 (16S rRNA gene 454 pyrosequencing, King George Island, Antarctica) http://dx.doi.org/10.7845/kjm.2016.6005
6.	Krause et al. 2020 (16S rRNA gene sequenced, Peru basin, South-East Equatorial Pacific – potentially 2 decades on abyssal seafloor) https://doi.org/10.1038/s41598-020-66361-7
While I agree that some of these papers have a different focus than the current study, I think that the findings of this study should be put into context with these papers.
I also appreciate that the authors have uploaded their raw sequencing data to the SRA, although I think it would be beneficial to also provide the processed ASV tables (with taxonomy) as well as metadata (e.g., any information on location, physicochemical parameters at the time of sample collection, etc.) as supplementary information. Ideally, any scripts used for analysis should also either be provided or a link to this on Github added.
Experimental design: See above related to discussing the findings of other Southern hemisphere plastisphere studies. This research is, however, still relevant and I think the experimental design has been carefully designed. The only thing I found slightly disappointing was to only have two replicates for each substrate type within each location – including at least three would have enabled further statistical testing. It is obviously not possible to include this retrospectively, but I hope the authors take this into account for future studies. This would have enabled more comparison within locations, which are where the largest differences in plastisphere composition between substrate types are thought to occur.
There are some further specific questions that I had below.
Validity of the findings: Overall I think that the authors have been careful in not overstating their results, however, they say in the abstract that the “study sheds light on the question of whether bacterial communities on plastic debris are shaped by the physicochemical properties of the substrate they grow on or by the marine environment in which the plastics are immersed”. Whilst it’s clear that overall the largest differences in community composition are due to location/other parameters related to this, they weren’t able to look for differences in community composition between the different substrates within the locations that they study and I therefore think that this as well as any other similar statements should be revised accordingly. I also think it would be interesting to pool the two PE substrates and the other two substrates in order to look for differences – on the NMDS plots for some locations it does look like there is slight separate grouping and I would be interested to see this investigated further. It would also be good to show the NMDS plot with weighted unifrac as well as the unweighted distance that is shown.
The authors do discuss this briefly (line 301), but I would have liked to see further discussion of the underlying differences between each sample location, e.g. temperature, salinity, light availability, given that the sampling was at different seasons for Northern/Southern hemisphere.
Additional comments: This was a nice, well-written paper that I think contributes nicely to our understanding of the plastisphere. Further to the above comments, I had a number of specific queries/comments:
Line 84 and others: note that the study referenced doesn’t use chitin. While I agree that this is a naturally occurring substrate, wood is usually included because it is assumed to be a relatively inert substrate in the ocean, whereas chitin is much more rapidly degraded.
Throughout: Note that Unifrac should be spelt with a ‘c’ and not a ‘q’.
Line 154: It’s not clear to me why the authors used the single-end DADA2 method when they had paired end data – were the reads joined prior to this? Please clarify.
Line 164: Was the tree de novo? Did the authors verify the validity of the tree? In my experience, amplicon sequences do not make robust trees and these usually do not reflect the generally accepted phylogeny. I would have preferred to see this step done via insertion into an existing tree (e.g. the SEPP method within QIIME2), particularly as this tree was presumably used for the beta diversity analyses.
Lines 182-187: at which phylogenetic level were these tests performed? And I assume that these are for differential abundance testing? There are many microbiome-specific methods (ANCOM, ALDeX, Corncob…) that I think would have been more appropriate here; while not completely necessary, I do think that more information needs to be provided here.
Line 191: Was this absolute count before rarefying? Related, the rarefaction curces in Fig. S1 should ideally show all samples, and should be before rarefying.
Line 252-257: What is meant by diversity? The number of ASVs? Relative abundance? Ranges for each of these eleven phyla would also be useful to add here.
Lines 264-265: Add references
Line 280: Does NCBI BLAST give any further indication to which taxa these are?
Fig. 2 legend: Replace “insignificant” with “non-significant”
Fig. 5: I think this figure would benefit from an additional colour scheme representing abundance or an additional column indicating the maximum relative abundance for each phylum as it is currently a bit difficult to discern the differences in abundance. Also, for the lower abundance phyla, are these each present on each replicate within the substrates? Something to indicate whether this is the case or not should be added.
Fig. 6: Are the “slices” shown here proportional to abundance? A more detailed description of this chart as well as an idea of the number of ASVs that each family encompasses should be added. I think showing either the family or genera as something like a heatmap showing the differences between substrates would also be useful – having this only at the phylum (i.e. Fig. 5) is a bit high to really have a good idea of the differences/similarities here.


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

Input:
Title: BIOGEOGRAPHY RATHER THAN SUBSTRATE TYPE DETERMINES BACTERIAL COLONIZATION DYNAMICS OF MARINE PLASTICS
Review round: 2
Reviewer: 1

Output:
Basic reporting: Dear Authors,

thanks for your rebuttal letter and for addressing the comments from both reviewers in your revised version. I found your manuscript very interesting and I do not have further comments.
Experimental design: I appreciated the inclusion of raw data and codes as suggested by the reviewer as well as supplementary data indicating sampling locations and environmental parameters.
Validity of the findings: I appreciate the authors' effort to address my previous comments and questions and I think now with the additions the manuscript has much improved.
Additional comments: No additional comments


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

Input:
Title: BIOGEOGRAPHY RATHER THAN SUBSTRATE TYPE DETERMINES BACTERIAL COLONIZATION DYNAMICS OF MARINE PLASTICS
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: I am pleased with the revisions made and think that most of my concerns as well as those of the other reviewers are now covered. I have only a few minor comments remaining:
- It was disappointing that the authors didn't try to include a combined analysis of the substrates (i.e. HDPE+LDPE and PA+PMMA), or comment on their choice not to do this.
- I am fine with the authors' reasoning to use only the single-ended sequencing data, but think this should be added to the text as (presumably) the data uploaded to the SRA is double-ended. If future researchers attempt to reuse this data then this may be relevant.
- I agree that their tree was probably fine, but maybe I didn't make my point/concern clear enough. In my past experience, creating a de novo tree with amplicon sequences (i.e. reads that cover only a small fraction of the 16S rRNA gene) has led to a tree where the majority of placements are fine, but there will often be something strange such as the Gammaproteobacteria being split into two groups, separated by the Alphaproteobacteria. I was therefore mainly getting at whether - as they do not provide the tree that they used, or a visualisation of it - they verified that it was actually correct according to the accepted phylogeny before using it for the unifrac analyses. SEPP is one method that I gave an example of, although not what the authors necessarily have to use - my only point was that if there were issues with the tree due to the short amplicon sequences (and I would be surprised if there were none) then insertion into a larger tree would alleviate these. Hopefully I have clarified my comment sufficiently now.
- "Insignificant" should also be switched to "non-significant" in Fig. 3.
- For Fig. 6 the authors explained this more thoroughly to me, but this also needs to be added to the figure legend. I have not previously come across such a plot and believe this may be the case for many others too. Explicitly stating exactly what this is and that e.g. that the size of a chuck is proportional to median relative abundance would be useful. I disagree that adding ASV counts would be misleading, as it would give readers an idea of the diversity within different groups (although they could choose to do this in another way - I only gave a suggestion) - there is currently not anything that illustrates whether e.g. all of the relative abundance accounted for by Bacteroidota members is due to only 3 ASVs while the relative abundance accounted for by Gammaproteobacteria is accounted for by 100 ASVs. This is clearly an extreme example but I do think it would be interesting to have something that gives the reader a better indication of the composition at lower taxonomic levels, whatever the authors prefer this to be. It seems odd to have nothing that gives the reader an idea of how the composition differs at very fine resolutions, particularly as they discuss things like the relative abundance of Vibrio spp. but give the reader no opportunity to visualise this, and in fact the first mention of this is in the discussion.


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: HABITAT EPHEMERALITY AFFECTS THE EVOLUTION OF CONTRASTING GROWTH STRATEGIES AND CANNIBALISM IN ANURAN LARVAE
Review round: 1
Reviewer: 1

Output:
Basic reporting: BASIC REPORTING
•	Clear, unambiguous, professional English language used throughout.
o	Yes, for the most part. See Specific Comments below for exceptions.
•	Intro & background to show context.
o	Yes, though some additional clarification would help. See Specific Comments below for exceptions.
•	Literature well referenced & relevant.
o	Yes, for the most part. See Specific Comments below for exceptions.
•	Structure conforms to PeerJ standards, discipline norm, or improved for clarity.
o	Yes, looks fine.
•	Figures are relevant, high quality, well-labelled & described.
o	Yes, although I think they could do with some additional detail in both the figures and the captions. See Specific Comments below.
•	Raw data supplied (see PeerJ policy).
o	Yes. Can the authors please explain the NAs in the data? Are they tadpoels that died during the experiment? How were the NAs dealt with in the analyses?

Vertebrate animal usage checks
•	Have you checked the authors ethical approval statement?
o	Yes, looks fine.
•	Were the experiments necessary and ethical?
o	Yes, no problems.
•	Have you checked our animal research policies?
o	Yes, looks fine.
Experimental design: EXPERIMENTAL DESIGN
•	Original primary research within Scope of the journal.
•	Research question well defined, relevant & meaningful. It is stated how the research fills an identified knowledge gap.
o	Somewhat. See Specific Comments below for exceptions, especially regarding the Introduction.
•	Rigorous investigation performed to a high technical & ethical standard.
o	For the most part. I have concerns regarding genetic diversity in the experiment and the inclusion of only a single population from each location. See Specific Comments below.
•	Methods described with sufficient detail & information to replicate.
o	For the most part. The descriptions of statistical analyses, in particular, are insufficiently detailed. See Specific Comments below.
Validity of the findings: VALIDITY OF THE FINDINGS
•	Impact and novelty not assessed.
•	Meaningful replication encouraged where rationale & benefit to literature is clearly stated.
o	Yes. It is especially important that this study be repeated with additional populations and that it be complimented by population-genetic studies to investigate some of the authors’ claims. See Specific Comments below.
•	All underlying data have been provided; they are robust, statistically sound, & controlled.
o	For the most part. See comment above regarding NAs. Also, considering habitat ephemerality is highlighted as a likely important selective pressure, I am surprised by the lack of a desiccation-risk treatment and accompanying control, as has been done with other taxa in studies by, for example, Denver, Gomez-Maestre, Buchholz, and others.
•	Speculation is welcome, but should be identified as such.
o	Some statements are made too strongly and presented somewhat axiomatically as explanations for the observed results despite a lack of data to support those claims. See Specific Comments below, especially regarding the Discussion.
•	Conclusions are well stated, linked to original research question, & limited to supporting results.
o	Somewhat, though some results are not fully explored (e.g., the big difference between insular and mainland in the abundant-food low-density treatment). In addition, conclusions regarding the potential for genetic differences to underpin the observed phenotypic differences, as well as a couple of other statements, seem to me to exceed the boundaries of the data without explicitly mentioning the speculative nature of those statements or alternative explanations. See Specific Comments below.
Additional comments: Specific Comments

Introduction
•	line 38 – this sentence is vague and doesn’t communicate much of anything. Consider something that is more direct (e.g., “ephemeral environments impose numerous selective pressures and have favored the evolution of...”)
•	line 40 – replace the slash with ‘and’
•	line 42 – add a comma between ‘stay’ and ‘heavily’
•	line 50 – adaptive responses to what?
•	lines 57-62 – can you clarify these statements? Are you saying that prior studies that examined differences in tadpole development time produced results that were confounded with phylogenetic relatedness or other variables? I would suggest that past work by Denver, Gomez-Maestre, Buchholz, and others has effectively isolated the effects of desiccation risk on development time. Also, the final sentence is confusing in the context of the rest of the paragraph, which talks about plasticity, which should evolve in reliably predictable but variable environments, but the final sentence seems to ask whether directional selection might favor the evolution of singular developmental strategies. Clarifying this paragraph will help explain the value of your study.

Methods
•	line 129-131 – were you able to track which matings the tadpoles in each replicate came from? If not, can you account for the possibility that your results might reflect, in part, outsized contributions of one or more families within treatments or replicates?
•	line 132-133 – did you measure the parents’ SVL and/or mass? Adult body size and body condition are known to affect tadpole size, development, morphology, etc. in multiple anuran taxa (see, e.g., Bennett, A.M. and Murray, D.L., 2014. Maternal body condition influences magnitude of anti-predator response in offspring. Proceedings of the Royal Society B: Biological Sciences, 281(1794), p.20141806.
•	line 161-162 – what distribution was specified for these models?
•	line 166-168 – I see you used AIC scores for model comparisons, but where did your z-score test stats some from? Wald tests? Please include these details.
•	An additional analysis that might improve your study would be a comparison of the relationship between larval period and weight at metamorphosis between island and mainland populations and between treatments (i.e., do the slopes differ?). This could generate an informative figure(s) if there are different slopes between locations/treatments. I see that you did part of this with Fig. S1, but there don’t seem to be any accompanying analyses.

Results
•	line 175 – the z-score is reported with a comma where there should be a period
•	line 183 – there is no Fig. 2B. Is this a typo?
•	line 194 and Table 1 – please explain the statistical tests used here. I see t-statistics but no explanation of the means used to approximate degrees of freedom for these t-tests. Did you use a specific R package to perform these (e.g., lmerTest)? If so, please cite the package(s). Also, please include SE for at least the model coefficients.
•	line 197 – ‘becoming’ should be ‘became’
•	General – can you perform post-hoc tests to report pairwise differences among the treatment/location groups with corrected p-values in the results shown in Figs. 2 & 3? You’ve shown only whether treatments had effects in general.
•	Figures
o	can you use those posthoc tests to add indications to your plots of which groups are significantly different from other groups? (E.g., line over pairs of boxplots with p-values or asterisks that are explained in the captions)
o	Please describe the box-and-whisker plots in the figure captions (e.g., thick middle line is median, boxes are interquartile ranges, whiskers are 1.5x IQR, points are individuals with values outside 1.5x IQR...s)

Discussion
•	line 223-227 – see comment above regarding analysis of and potential figure(s) for the possibility different relationships between larval period and weight at metamorphosis among groups. I think it would be nice to see this addressed more explicitly.
•	line 233-234 – I see positive correlations in all panels except the mainland abundant-food low-density one. Also, the caption for Fig. S1 contradicts the statement at these lines.
•	line 239 – 243 – I would certainly expect genetic differences given the split in the Cenozoic and the subsequent lack of gene flow, but you do not present data that show genetic differences that are the bases of the phenotypic differences that you show in your study. Since anuran tadpoles are known to be highly plastic along various phenotypic axes, it seems a good idea to mention the possibility of plasticity playing some role in the observed differences. Also, is the insular habitat genuinely “unpredictable” as suggested on line 220? Or might there be reliable cues in the island habitat that could have favored the evolution of greater plasticity among island tadpoles?
•	line 246 – is the fact that each location is represented by a single population stated clearly in the methods?
•	line 247-250 – have you or anyone else investigated the populations genetics of the mainland and insular populations? how reasonable is it to assume homogeneity with each location?
•	line 253 – please clarify how it might ‘drive’ faster larval growth
•	line 257 – I think the indirect fitness/kin selection hypothesis is a bit overstated here, especially since you cannot distinguish between scavenging and cannibalism that actually consists of consuming live kin. It may be that the mainland tadpoles simply didn’t do as well in these experimental conditions and were quickly eaten after dying of other causes. Can you perform an analysis using only confirmed cannibalism of live kin, or are there not sufficient data?
•	line 278-279 – I think this is stated too strongly. It is still possible that some portion of the observed differences arose via plasticity. Additional study would be required to demonstrate the point made in these lines.
•	General – can you perhaps provide further hypotheses for the dramatic differences between insular and mainland populations’ weight-larval period relationships in the abundant-food low-density treatment (Fig. S1)?

References
•	please refer to the PeerJ references instructions: https://peerj.com/about/author-instructions/#reference-format
•	journal titles should be given in full and italicized
•	please make sure other instructions are also followed


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: HABITAT EPHEMERALITY AFFECTS THE EVOLUTION OF CONTRASTING GROWTH STRATEGIES AND CANNIBALISM IN ANURAN LARVAE
Review round: 1
Reviewer: 2

Output:
Basic reporting: Language and clarity could be improved in a few places. Listed below are small edit suggestions.

Line 34: typo B. orientalis

Edit introduction first few sentences – for example:
Line 38: central to the [study of] environmental adaptations of animals?
Line 42: heavily influences
Line 42: some unclear sentence structure (who is “themselves”)?

Line 175: typo 2.35

Line 183: Fig. 2B should just be Fig. 2?

Line 197: became

Figure 1: I’m curious, are the streams on Jeju island disconnected puddles most of the time vs a flowing stream? How quickly does a stream go from flooded to puddles?

Fig S1: It may be better to have weight on the same scale between the 2 panels to allow for a direct comparison
Experimental design: This manuscript shows a well-conducted experiment evaluating whether there are evolved differences between a mainland and island population of Bombina orientalis, which differ in stream ephemerality. They test clear hypotheses that are well supported in the literature.

A few spots to clarify in methods:
Line 117: Clarify that these streams represent a single population – otherwise this is not clear until the discussion

Line 123-124: I’m unclear on your number of families – are you reporting all parents or the number of females that laid eggs?

Line 133: It could be helpful to provide a summarizing statement clarifying sample size in the experiment – how many different families are represented in the experiment? Are eggs from each family/clutch split between treatments or all in one experimental container?
Validity of the findings: Though only one mainland/non-ephemeral and one Jeju island/ephemeral population are used in the study, the authors are sufficiently careful not to over-reach the implications of their results.
Additional comments: The authors conclude that the observed differences have a genetic basis (i.e. lines 240, 280), yet since parents were collected directly from the field, environmental maternal/parental effects cannot be ruled out. Maternal effects can have a large effect on anuran phenotypes (see discussion of maternal effects in common garden experiments in Laugen et al 2005). For instance, in another cannibalistic tadpole, spadefoot toads, higher condition mothers produce larger eggs which become larger and more carnivorous tadpoles (Martin & Pfennig 2010). While it is impractical to rear the frogs for one or more generations under common conditions to minimize maternal effects, some studies measure egg size as a proxy for maternal investment and parental effects (i.e. Urszán et al 2015). I suggest the authors add a brief note or discussion acknowledging that maternal effects cannot be ruled out in this study.

Laugen, A. T., Kruuk, L. E., Laurila, A., Räsänen, K., Stone, J., & Merilä, J. (2005). Quantitative genetics of larval life-history traits in Rana temporaria in different environmental conditions. Genetics Research, 86(3), 161-170.

Martin, R. A., & Pfennig, D. W. (2010). Maternal investment influences expression of resource polymorphism in amphibians: implications for the evolution of novel resource-use phenotypes. PLoS One, 5(2), e9117.

Urszán, T. J., Török, J., Hettyey, A., Garamszegi, L. Z., & Herczeg, G. (2015). Behavioural consistency and life history of Rana dalmatina tadpoles. Oecologia, 178(1), 129-140.


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: HABITAT EPHEMERALITY AFFECTS THE EVOLUTION OF CONTRASTING GROWTH STRATEGIES AND CANNIBALISM IN ANURAN LARVAE
Review round: 1
Reviewer: 3

Output:
Basic reporting: I very much enjoyed reading this manuscript. The system is appropriate to the questions, and the authors have done an excellent job explaining the natural history, and how it fits with these questions, to the reader. The work is well-designed and the conclusions are clear and interesting.

1) This is a well-organized and largely well-written paper. I do think it would benefit from just a bit more proofreading/language editing (although it is again well done). e.g., ln 196/7 I think there's a proofreading thing, and in several places some precise word choice will improve the manuscript (e.g., ln 238 replace "grew" with "developed"). This is a minor concern, but it is a great paper and I would like to see it have the biggest impact.

2) The literature review and use of references was good. It certainly isn't exhaustive, and there are some places where the classics might play a bigger role (e.g., citing some more broad kin selection papers rather than anuran empirical papers only), but again this is fairly minor. The authors covered the broad topics well.

3) The paper is professionally structured, and I have no concerns there. The raw data seem easy to access and interpret.

4) This work was self-contained, and had a complete and solid narrative structure.
Experimental design: 1) This is well within the aims and scope of the journal

2) The research questions, both particular (104-109) and general (ln 60-62) were well-defined and addressed by the study and Discussion.

3) The work was well-conducted. It may have been nice to be able to keep track of families (e.g., with a random effect), but by mixing tadpoles from many families the authors have exceeded the standards in this field. I have no concerns about the quality of the work performed.

4) The methods were well-described. Indeed, the authors did an exceptional job of "telling the story".
Validity of the findings: The underlying data are provided and are straightforward and easy to interpret.

The statistics seem entirely appropriate, and the authors have done a nice job of including tables/figures for inspection and also telling a clear and and interesting (but not repetitive) story in text.

The conclusions seem safe to me, although I would encourage the authors to make a clear distinction between "splits" that are justified by significant interactions and ones that are not. If there's no interaction, there's no interaction, and follow up "differences" can be mentioned but should not be emphasized (ln 183).
Additional comments: The authors indicate fairly strongly that differences among habitats are likely genetic, and this is a theme throughout the paper (it even seems a prediction that is being tested).

Most conservatively, several generations should be bred in the lab when testing this hypothesis to remove environmental effects on parents that are transmitted as maternal effects. That is obviously impractical here. This makes no difference to the interest of the work, so I would simply re-write to suggest that differences may be genetic (or may not be) - because plasticity and genetic differences should push populations in the same direction in response to selective pressures, it genuinely makes no difference here.

I would also think a bit about whether adult body size differences matter. Does this put the differences in mass at metamorphosis in any different context? Maybe yes, maybe no. I think the potential interactions address this to some extent.


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: HABITAT EPHEMERALITY AFFECTS THE EVOLUTION OF CONTRASTING GROWTH STRATEGIES AND CANNIBALISM IN ANURAN LARVAE
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: I am satisfied that the authors addressed each point raised. I think this is a nice paper that is ready for acceptance and that the authors' data and presentation of their data will make for nice contributions to PeerJ and to the field.


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: CAPTURING AND ANALYZING PATTERN DIVERSITY: AN EXAMPLE USING THE MELANISTIC SPOTTED PATTERNS OF LEOPARD GECKOS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Capturing and analyzing pattern diversity: an example using the melanistic spotted patterns of leopard geckos by Glimm et al.

I found this project very interesting and although I must confess that I cannot comment on the methods, because I don't have the computational background, looks like the automatization and capture methods are adequate. I have made a few comments directly on the PDF, but I would mention and explain these here. I also give away my anonymity statutes and the authors can contact me directly if needed. The paper really needs a throughout review of the format, the citations are inconsistent, sometimes et al., is written without the period or without the comma.

Juan Diego Daza (juand.daza@gmail.com)
Experimental design: Regarding the seven regions delimited, some regions seems a little bit arbitrary. I also noticed that the manus and pes were not included, despite the fact that they exhibit important variation. Portions of the cervical and sacral regions not included, but I guess this was done to avoid problems causes by gradual transition from one pattern to the other in adjacent regions. This is not necessary wrong, but it should be stated (I am sorry if you already did this).  I also noticed that the sample of 25 geckos, although includes a good representation of the morphs available, it is not complete. I wonder if it would be worth including the two melanistic extremes (even from the theoretical point of view); Leopard geckos are know to have complete melanistic and albino morphs. This is probably not needed to include, but then again, at least mention this on the background information.  I don't think this last point is critical, cause I don't expect a combination of these extreme forms with he morphs identified (e.g. a gecko with a white head and pigmented trunk).
Finally, this could be a matter of semantics, but melanistic while referring to black pigments, technically won't be classified as color, but as shade. Black since it doesn't reflect light, is not a color.
Validity of the findings: I think the paper has very interesting findings, especially the idea that different modules in the gecko body are independent. By the way, makes me wonder why the term module is not use?
Additional comments: I find this study very innovative for the study of gecko melanism. I think the variation observed can be expanded, especially if including the extremes is a possibility.


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: CAPTURING AND ANALYZING PATTERN DIVERSITY: AN EXAMPLE USING THE MELANISTIC SPOTTED PATTERNS OF LEOPARD GECKOS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Tilmann Glimm and colleagues present in this manuscript a comprehensive strategy to quantify pattern variation. Their strategy uses 14 indices that capture characteristics of spotted patterns. These indices can then be used to compare patterns on body parts or between individuals using PCA type of analyses. Within the PCA space they also provide two normalized distance measures that allow to statistically compare patterns. They us this strategy on a set of gecko images and obtain novel insights into their pattern development. They also, interestingly, note that their strategy can be used to compare mathematical models of pattern development with observational data.

I read this manuscript with much interest and I found that the complex concepts are incredibly clearly explained. I think this study will provide a valuable benchmark for other researchers interested in studying pattern variation, which to me is notoriously difficult to quantify. The strategies to cope with sampling noise, developmental noise and individual differences seems unique and well thought out. I have only small suggestions and questions that I hope the authors could maybe elaborate a bit on.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Maybe one larger comment that I think would benefit the community is to make sure the pipeline is easily accessible and well annotated. I am not a Matlab user myself, because it is not a free software, so if I would want to use your scripts, I would have to follow a steep learning curve.

L58: These studies use landmarks to align images by transforming them to the same size and shape. The color patterns are then compared pixel by pixel, assuming that each pixels now presents a homologous feature.

L64: missing period after parentheses.

L68-79: I strongly agree. I wonder if saliency maps which should have the power to highlight important features in the images will provide possibilities for quantitative pattern recognition. https://arxiv.org/pdf/1312.6034.pdf

Also, distance scores can still be obtained from the machine learning algorithm, which provides a quantitative measure of similarity: see for example, https://advances.sciencemag.org/content/5/8/eaaw4967

L192-205: I am hoping the authors could elaborate on how this trial and error strategy would work for other studies with different organisms. Is there potential for bias, is image standardization necessary, …?

L211-227: I think I understand how this works for melanistic spots, but what to do with other color patterns (e.g.  yellow or red spots) in other organisms? What would be the advantage over other automated pixel classification methods like k-means clustering or watershed algorithm.

L213: How does the green channel indicate intensity, rather than R or B? Could a HSV (hue, saturation, value) color space be more appropriate?

L216-217: instead of ‘determining by eye’, is it possible to get histogram distributions of RGB values and see where the threshold falls that separates RGB values of spots from background?

L233: How does the 350 pixels compare to the resolution of the images?

L254-260:

Can the overall absence of pattern also be included as an index?

All indices seem to focus on ‘spots’. How well would they perform on complex patterns of stripes or curves?

L563: What are these stages, days?

L605: Yes. https://www.sciencedirect.com/science/article/pii/S0960982219313168 and https://royalsocietypublishing.org/doi/10.1098/rspb.2020.1267

L664: duplicated period

The reference manager is mistakenly not recognizing ‘van’ as the first part of a last name:

L720: Van Belleghem S.M.

L724: van den Berg C.P.


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: INDEPENDENT VALIDATION OF DOWNSCALED CLIMATE ESTIMATES FROM A COASTAL ALASKA WATERSHED USING LOCAL HISTORICAL WEATHER JOURNALS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The writing is generally clear and concise. I do think that more literature on downscaling and validations of climate downscaling could be reviewed in the Introduction. It would establish more context for the novelty of this validation to know that most downscaling validations are either not done at all, or are done using non-independent cross-validation approaches.

While this study is a novel and useful evaluation of the ClimateNA downscaled outputs, I’m not sure that it’s a “cross-validation” per se. Whereas cross-validation is a resampling technique that entails data splitting and model training/evaluation with partial datasets, this study uses an independent dataset to validate or evaluate the ClimateNA data. My suggestion would be to change “cross-validation” to “validation” or “evaluation” throughout the paper. (To be honest, I think calling this a cross-validation actually sells the analysis short. Independent validation is, in many ways, the gold standard of model evaluation whereas cross-validation is what we settle for when we lack independent data.) The title is similarly a bit confusing in this respect. I would suggest something more direct (and compelling) like “Independent validation of downscaled climate estimates from a coastal Alaska watershed using local historical weather journals”.

It would be nice to see a bit more background on Allen Haselborg’s journals presented in the introduction. These are such a novel and rich historical dataset that it seems somewhat unjust to bury them in the Methods. I think the authors would be justified to move the entire “Study area description” from the Methods to the Introduction and simply start the Methods section with “Data acquisition”. Editorial advice might be useful here too.

On figures, I didn’t want to go deep down a rabbit hole of figure rebuilding, but I think there are simple changes that could easily be made to the figures to make them much more useful in terms of interpretation of the results. In fact, just my own plotting the data in different ways raised a few new questions/discussion points in my mind, and I think could form the basis for a bit more Discussion. I have provided some examples in the specific comments below.
Experimental design: The research question is well defined in the Introduction and is a useful contribution. As noted above, the novelty and importance of the research could be better highlighted with a more comprehensive literature review (which, as mentioned above, I’m confident would expose an important gap to fill that this paper helps address).

The streamflow calculation is an interesting addition, but it wasn’t totally clear to me how it was implemented across a larger region for the Hasselborg observations. I assume that the authors used the single data point from Hasselborg for temp & precip and the consequent differences in flow across the grid cells would be all due to elevation. In that case, were the ClimateNA streamflow calculations done based on a single data point at the Hasselborg cabin Lat/Long, or was data pulled from ClimateNA for each grid cell (in which case differences are due to differences not just in elevation but also in temperature and precipitation at each grid cell). This should be clarified. I think the two comparison options here ask fundamentally different questions.
Validity of the findings: All relevant data and R code were provided. I was able to run the code and confirm the results.

The Discussion is generally well written, but left me wanting more. It would be interesting and informative to have a bit more context for the results presented here. The most obvious context to me (given our 2019 paper) is a comparison to other validations of the ClimateNA software. I think the results presented here are largely in line with what we found in our analysis, which is exciting and would be interesting to discuss a bit further. I’m not suggesting this simply to highlight our own work (honest!). I’m just not aware of other similar validations of ClimateNA or other downscaling products, but that would be something also to discuss. Are other historical climate records available from the region? From elsewhere? Can we use this approach in larger-scale or wider-breadth validation efforts or is this really a one-off validation for this particular local area? The authors note that there were a few weather stations in the Mole River area (though not in close proximity to the Homestead, and I’m not certain on the periods of record). I would be interested to see if validations against these stations’ data showed similar patterns to the Hasselborg journals. Not suggesting this be added to the current manuscript, but could be put forward as a possible future analysis.

An obvious limitation of the current research is that it only considered a very small geographic region, so results should be generalised with caution (i.e. across the larger coverage of the ClimateNA software). This should be stated a bit more obviously I think. This point also offers an opportunity to discuss historic observation data as a potential source of validation across the continent for a more generalisable validation.
Additional comments: L40-43 – The abstract jumps a bit abruptly to reporting on stream flow. Suggest revising to include a general statement about calculating stream flow comparisons from the data, which may catch readers off-guard if they are anticipating a climatic comparison only.

L50-53 – A bit jargony. Would be useful to either (1) limit the discussion to statistical downscaling (what ClimateNA does) and explain what that is, or (2) provide a statement for each downscaling approach and identify which applies to ClimateNA.

L55-57 – So our 2019 paper doesn’t really support this statement (though I don’t disagree with it). More relevant to the paper here, results from our 2019 paper suggested that ClimateNA (in addition to being user-friendly and geographically flexible) produced downscaled data that were among the more accurate of those we considered (at least in our study area in the Rocky Mountains). BUT, like this paper, we also found biases in space and elevation. This paper looks more at biases in time, so the two analyses complement each other well. I also think our 2019 paper is useful to the current manuscript by providing some rationale for ONLY looking at ClimateNA in this validation, rather than at a suite of downscaling models.

L79-80 – Suggest: “but their LOCAL accuracy…”. Landscape/regional/continental scale validations (and cross-validations) of downscaled data are much more common using weather station networks (including during their development, as with ClimateNA).

L80-87 – This is an important section that would benefit from a bit more background on what statistical downscaling is and how it relates to topography (see comment on L50-53 above). Accurate DEM data are critical, even simply to implement ClimateNA, particularly at smaller scales/extents. The implications of topographically complex terrain will be more obvious if the reader understands the critical link between downscaling and DEMs.

L82 – Suggest “masl” or write out “metres above sea level” since we’re talking XY and Z distances in the same sentence.

L124 – Add the version of ClimateNA used (the algorithm and base datasets can change between versions).

L205-209 – This is a really interesting result. Potentially has to do with a bounding algorithm of some kind that may be built into ClimateNA (and other downscaling models) to prevent exponentially high/low predictions. Hopefully Tongli Wang is a reviewer on this paper also and can comment.

L215-216 – For context compared to another validation of ClimateNA, in Roberts et al. 2019 we found a similar trend in our comparison, with ClimateNA generally tending to overestimate monthly temperature, particularly at lower (<1000 masl) and higher (>2000 masl) elevations, and either highly accurate or slightly underestimating at middle elevations (1000-2000 masl).

L262-267 – The hypothesis about the PDO driving bias in ClimateNA is well defined here, but ClimateNA likely also incorporates such phenomena in its data/algorithm. It would be interesting to hear more about how this divergence might emerge, particularly at the very local scale at which the authors are working (again, hopefully Tongli is also a reviewer). In other words, perhaps ClimateNA does well with the PDO and other oscillations on a continental scale, but less well locally or during years of oscillation shift. I’m not sure, but a bit more explanation here of why the authors think PDO is the culprit (other than the coincidental timing) would be useful.

Figure 1 – This is a nice map of the river basin, but is a bit lost between the huge AK key map and scale/north arrow. Can those components be scaled down and the map scaled up? Hard to tell how big it will all be once sized for the journal, but I’m thinking one column wide? If that’s the case, the map will be almost too small to read.

Figure 4 – Could be nice to see the residual figure presented in the same orientation as Figure 3 (stacked, with date stretched across). I don’t get a lot out of the residual plots beyond the inflection of the loess trendline. I was trying to think if there’s a way to present the actuals and residuals together to offer a bit more interpretability. When I plot them together, the peaks & troughs in the residuals become much more evident in terms of timing and seasonality. Not necessary to use this approach, just a suggestion to make the residual patterns a bit more visually evident (also see next comment). Also suggest keeping at least the vertical panel axes so it’s easier to see seasonality within years. Same with temperature would also be useful.

[See alternative precipitation plot.]

An alternative to including the loess splines to demonstrate the deviation of residuals in later years might be to show something like the cumulative residual over time, which visualises bias changes in the model (ClimateNA) over time. This is not a *typical* way to present these data, but helps accentuate the divergence of residuals in later years without the need for a loess spline implementation. (On that note, the loess spline implementation needs a bit more background explanation/rationale if it’s going to be shown on the plot.)

[See cumulative residual plot.]

Figure 5 – I think using boxplots rather than plotting means and SD for these plots would increase the interpretability and identify other interesting patterns in the residuals. (Also, the precipitation residuals are somewhat negatively skewed, making means and SDs somewhat suboptimal.) For example, the tighter distribution of summer precip residuals is an interesting pattern worth exploring, and I would be interested in the severe outlier in spring temperature residuals (a point that is hidden by mean/SD plots).

[See boxplot.]


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: INDEPENDENT VALIDATION OF DOWNSCALED CLIMATE ESTIMATES FROM A COASTAL ALASKA WATERSHED USING LOCAL HISTORICAL WEATHER JOURNALS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Very clear and concise report.  It was clear what your questions/hypotheses were and the results were relevant to the questions.  Good use of references.

I have no suggestion for changes.
Experimental design: Excellent design.  Good structure to lay out the results of your main objectives and a good example of applying in a hydrologic context.
Validity of the findings: No suggested changes.
Additional comments: I'm feel privileged to have the opportunity to review this paper as it was a fun to read. I don't have suggestions for major revisions.  Of course, reading this led me to ask several questions about ClimateNA - which is to say your point about needing "further cross-validation research" is highlighted and this research provides a good model to build future research on.


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: INDEPENDENT VALIDATION OF DOWNSCALED CLIMATE ESTIMATES FROM A COASTAL ALASKA WATERSHED USING LOCAL HISTORICAL WEATHER JOURNALS
Review round: 2
Reviewer: 1

Output:
Basic reporting: Very good. No further comments.
Experimental design: No comments.
Validity of the findings: No comments.
Additional comments: I think this version of the mansucript is much improved. While the science was robust in the previous version also, the additions to the Intro and Discussion specifically help highlight the novelty and importance of the work, and the clarity added around the methodology is welcome.


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: SEAGRASS CONTRIBUTION TO BLUE CARBON IN A SHALLOW KARSTIC COASTAL AREA OF THE GULF OF MEXICO
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment, see below
Experimental design: No comment, see below
Validity of the findings: No comment, see below
Additional comments: This paper assessing the carbon stocks in Los Petenes Biosphere Reserve (LPBR) in Mexico is of interest as it explores the carbon storage using multiple species and different water depths, which are two factors known to affect the carbon storage capacity in seagrass meadows. The manuscript is well written (I noticed, however, some grammatical errors) and I think the main issue is the presentation of the data and I have given some suggestions to that in the detailed comments below. Although, not included in the study but a comparison between the carbon storage within the MPA and outside would have been highly interesting, as well as a comparison with unvegetated sediments, which would have shown the contribution from seagrass meadows to the carbon storage as well as given an indication on the general accumulation of carbon in the area (in relation to for instance hydrodynamics).
Specific comments:

Introduction
Line 44: I suggest replacing “their” with “seagrasses” and place “their” and the second part of the sentence.
Line 52: Write out salt marshes.
Line 55-56: Please revise this statement, 50% of the carbon buried in marine sediments is found in all coastal blue carbon habitats combined (i.e. mangrove, salt marshes and seagrass). See for instance Duarte et al. 2013 - The role of coastal plant communities for climate change mitigation and adaptation.
Line 76: Please change to “water depth”.
Line 85-86: Check the grammar, …how much “that” is of autochthonous “origin”?
Line 90: Corresponds “to” 30%?
Lines 91-93: Please add a reference to this statement.
Lines 93-95: This sounds unreasonable, please consider revising. There are a lot of areas where seagrasses are increasing in area. See e.g. de los Santos et al. 2019 - Recent trend reversal for declining European seagrass meadows.
Line 116: Please change to “water depth”.

Methods
Line 126: The abbreviation LPBR should be moved to the introduction where the name is presented for the first time.
Line 127: Should it be “marine” reserve?
Lines 147-148: …water quality samples and “vegetation samples” were collected?
Lines 151-153: Please rephrase this sentence, “making measurements at 50 cm depth intervals from the surface to the bottom”?
Lines 176-178: Was no ground truthing conducted at the site?
Line 185: Once “cleaned”
Line 199: If the known sediment depth is 8 cm, why extrapolate to 1 m? This gives a higher carbon storage than the actual measured as well as a highly uncertain estimate of the stock, given only 8 cm were measured and 92 cm were extrapolated. I fully understand that 1 m sediment depth was used for comparison and I suggest that these cores should instead be excluded from those comparisons. I also think that these cores add to the natural variability of carbon storage, if only 8 cm has been accumulated, that site might not be the most efficient in carbon trapping.
Line 201: Were the cores correlated to the compaction or was the compaction only measured?
Line 204: the “mid-section” of each interval?
Line 211: LOI was used to determine OM?

Results
Line 281-282: I don’t understand the numbers, %OM (4-61%), %Corg (4-28%). Higher compared to what?
Lines 282-283: But there seems not to be a gradual increase in %Cing?

Discussion
Lines 351-356: This is a long sentence, please consider divide it into two.
Line 359: Should be fig 7?
Line 440: Should be fig 7?
Line 463: This is more of a general conclusion, please consider to move to “conclusion”.
Lines 470-475. The estimated loss of 130.8 Tg should be seen as a maximum, given that all of the carbon is remineralized and released to the atmosphere. This needs to be clear. Also, is this for 1 m of sediment?

Figures and tables.

Fig 6 and fig 8 are not referred to in the text. Or fig 6 is referred as 7.

Fig. 1. Is the black line in fig to the left the reserve boundaries?
Fig. 4. Please change to “species”. There is no mention in the caption what fig a-f stands for, neither does the figure show which depth the circles belong to. I don’t know what this figure adds to the study, please consider removing.
Fig 5. This is a nice figure. Please write what the abbreviations stands for (AB, S etc). I strongly suggest to present the carbon stocks of the different species separately in relation to water depth.
Fig 6. Is this sedimentary carbon or biomass or both? Why is this figure not reported in the results but only referred to in the discussion? Are these stocks including area? I suggest a better way to represent this would be to have a A and B figure where B is a bar graph showing the stocks, that would be easier to interpret.
Fig 7. Numbers represent each water depth? How could you find mangrove sediment at 4 m? This could also be a A and B figure, where B shows the results from the model as mean ± SD contribution of the different sources for each water depth.
Fig. 8 is very illustrative. Instead of showing the isotope signal, it would be more interesting to show the relative contribution from land/mangrove, which seem to decrease from shore. Is the thick blue line representing water discharge?
Table 2. Is MO in fact OM? Why is %Corg and OM almost equal at water depth 5.
Table 4. The first sediment carbon content, to what sediment depth is that calculated?
Table 6. I find it odd that seagrass didn’t contribute at all to the sedimentary carbon pool at 1 m


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: SEAGRASS CONTRIBUTION TO BLUE CARBON IN A SHALLOW KARSTIC COASTAL AREA OF THE GULF OF MEXICO
Review round: 1
Reviewer: 2

Output:
Basic reporting: Language:
The English language is not clear and should be improved. There are very long sentences and grammar errors throughout the manuscript. I recommend a careful review of language. I provide here some examples from the abstract, for full review throughout the manuscript please see specific comments on each section:

L29: Authors use a noun (storage) instead of a verb (store)

L30: “The seagrass community extent for 149,613 ha” should be “The seagrass community extends …”

L33: “source” should be “sources”

L33-34: “If the seagrass extension in the LPBR lost through natural or
anthropogenic impacts could contribute with 130 Tg CO2eq emissions”.
Please rewrite, something like this would be better: “If LPBR seagrass meadows are lost  due to natural or anthropogenic impacts, 130 Tg CO2eq emissions could be released.”

Background references:
Overall introduction is well documented and referenced but the structure needs to be improved. Authors should try to have one clear and main idea per paragraph, and restructure the information in a more logical order.

Manuscript structure:
the manuscript follows the appropriate sections.

Figures and Tables:
Figures and tables do not follow acceptable format and content.  Specifically:

-Fig 1. Panels in Fig 1 need to be labeled with letters. More information on panel consisting of Sentinel 2a image is needed.
-Fig 2. Authors need to provide much more information in Figure heading and need to follow the format requirements form the journal, like labeling each panel with letters. What are insets on each photo?
-Fig 4. What does a, b, c, d, e ,f ,g , h , i and j mean?
-Fig 5. Please split this data at least in two independent panels: One for biomass stocks and one for sediment stocks.
-Fig 7. Where does the mangrove sediment and mangrove leaves data come from?? Not reported in methods. If these values correspond to data previously reported it needs to be specified in the fig heading.
-Fig 7 and Fig 8 are not mentioned in the text.

-Table 1 summarizes water quality data but is not referred in the text.
L172: This is the first table appearing on the text and it is referred as Table 2. But Table 2 summarizes sediment characteristics, not seagrass coverage as stated. Should it be Supplementary Table 2? If so, supplementary Table S1 is not appearing on the text neither. Please make sure that tables are labeled in the right order, following their appearance on the text.
Supplementary Table 2 needs major revision:
-First, all abbreviations for type of meadow need to be written in full.
-In MxMa (mixed seagrass meadow with macroalgae), no data on which macroalgae sp are present neither their relative contribution.
-In MxSf (mixed seagrass meadow dominated by S. filiforme), shoot density and cover of H. wriigthi and S. filiforme are similar. Why do authors consider it as dominated by S. filiforme? Which parameter do they base this classification on?
-In Sf (monospecific meadow of S. filiforme), why is there info on T. testudinum and H. wriigthi if it is a monospecifc meadow of S. filiforme?
-please consider adding the N of samples per each type of meadow, along the mean SeM, median and Range.

Table 1, 2 and 3. Please provide more information on table header and write variables in full.
Table 2 and 6. "MO" should be "OM". Also consider writing it in full.

Raw data: Supplementary Data set and  Supplementary Data cores need clarification on what variables are in each column and units, etc.

Hypothesis: Authors do not state a clear hypothesis. Please provide a clear hypothesis at the end of the introduction section.
Experimental design: This study falls within the aims and scope of this journal.

Authors identify the following knowledge gaps:
At the end of second paragraph, authors identify a first knowledge gap: (L78) “However, insufficient reports exist regarding how the structural complexity of seagrasses is related with carbon sources and their ability to store organic carbon in subtropical regions with the influence of groundwater.”
Then (L81): “Estimates of carbon stocks of seagrass meadows across the world are derived from little data, resulting in the tendency to generalize global carbon stocks in these habitats (Serrano et al., 2014).”
And in third paragraph (L85): “However, research questions remain about these estimates, such as how much of the organic carbon stock in seagrass meadows is allochthonous and how much is autochthonous? (Kennedy et al., 2010; Garcias-Bonet et al., 2019). This question must be addressed at the regional level since the conditions where seagrass meadows are distributed are specific to each region and have implications related to ecosystem connectivity.”

However, Identification of knowledge gaps should be stated more clearly. For instance:
- scarcity of data on the relation between C stocks and seagrass complexity for subtropical regions.
- scarcity of data on C stocks for subtropical seagrasses
- scarcity of data on the contribution of auto- vs allochthonous materials in C stocks

Methodology used here do not follow the highest standards. specific comments:
I think a general rearrangement of Material and methods is needed. Info on stations and surveys should not be included only in the subsection of water quality, it is confusing in the present form.
No clear when sampling events toke place. No clarity in the number of stations and which parameters were assessed in each one.
Authors identify 5 bottom types but data on seagrass coverage is not supporting such classification.
L170-171: “For the classification of the image, four classes were considered based on an analysis of conglomerates with 80% similarity,…” Shouldn’t be 5 classes (i.e. Tt, Sf, MxMa, MxSf, and S)?
Also, provide info on which seagrass spp. are found in mixed meadows.
In MxSf (mixed seagrass meadow dominated by S. filiforme), shoot density and cover of H. wriigthi and S. filiforme are similar. Why do authors consider it as dominated by S. filiforme? Which parameter do they base this classification on?
In Sf (monospecific meadow of S. filiforme), why is there data on T. testudinum and H. wriigthi if it is a monospecifc meadow of S. filiforme?

L 181: “three quadrants of 1 m2 in four 25 m transects (4 quadrants by station)”. Please provide more information here. Are these stations the same as in Fig.1? I do not understand exactly how many 1m2 quadrats were sampled and how they were distributed. Please clarify.

L190-193: “To estimate the average carbon content in the biomass (Cbio) of seagrass by the above and belowground components, the values of the dry weights (g Dw m-2) were converted to carbon equivalents using conversion factors 0.34 and 0.35, respectively (Fourqurean et al., 2012a), after which these values were finally extrapolated to Mg C ha-1.”

The way authors calculate Carbon content in above and belowground biomass is not adequate. Authors used conversion factors to calculate Carbon content from tissue dry weight values using values reported in Fourqurean et al 2012a.
C content ranges widely depending on seagrass species and location. Therefore I strongly suggest that actual concentration of C in above and belowground tissues is analyzed for each seagrass species and type of meadow in order to provide accurate estimates of biomass C stocks, which is one of the main objectives of this study.

Moreover, authors refer to Fourqurean et al 2012a et al for the conversation factors, however, in this work Fourqurean et al. used mean values extracted from Duarte 1990 and other three studies that reported high variability in C content. For example Duarte 1990 reported C content ranging from 24 to 44%.
And here, there is a more recent example of the great variability of C content in seagrass leaves is the extensive work from Duarte et al 2018 with data from more than 200 seagrass tissue samples. Range: 14.98 – 42.58%.

Therefore, I think that data on above and belowground biomass cannot be published in the current form.

L214-215: “The percentage of organic carbon (Corg) was calculated as the difference between inorganic carbon (Cing %) and total carbon (TC %).”
Standard protocols require an acidification step prior to the analysis of C in order to remove carbonates. This step is especially important in carbonate rich sediments like the ones from the study site.
Authors need to support their choose of not acidifying sediments. Sediment C stocks are calculated based on these values, and, therefore, this is a crucial analysis in this work, which in this current form does not follow the standard protocols.

I suggest that authors use more recent models to evaluate the contribution of different sources to the organic carbon in their sediments. Authors could use as well values on delta 15N and not only delta 13C.
Available Bayesian models in R packages are an easy and comprehensive tools that authors could explore. For instance, see Parnell et al 2016.
Parnell, A. (2016). Simmr: a stable isotope mixing model. R package version 0.3.
https://CRAN.R-project.org/package=simmr (accessed Janauary 19, 2016).
Validity of the findings: Raw data has been provided, however, more information needs to be added regarding meaning of acronyms and abbreviations and units in column variables on datasets.
I suggest that authors include an explanatory paragraph accompanying the datasets.

Conclusions are based on data that I believe needs major revision.
Additional comments: No additional comments


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

Input:
Title: SEAGRASS CONTRIBUTION TO BLUE CARBON IN A SHALLOW KARSTIC COASTAL AREA OF THE GULF OF MEXICO
Review round: 2
Reviewer: 1

Output:
Basic reporting: I have reviewed the new manuscript and changes made by the authors and I have no further comments.
Experimental design: -
Validity of the findings: -
Additional comments: I have reviewed the new manuscript and changes made by the authors and I have no further comments.


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

Input:
Title: ACOUSTIC INDIVIDUALITY IN THE HISSING CALLS OF THE MALE BLACK GROUSE (LYRURUS TETRIX)
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is concise and well written overall, and addresses an interesting question, that is, whether calls of a bird of the Galliformes order are individual specific.

There are however a number of points that should be clarified and expanded on, especially in the method and result section.
It would be helpful to know which variables were measured (could be included as Table). How where they selected? This should be explained in more detail. In addition, 29 variables are quite a lot. Should not the number of variables be smaller than the number of cases (here 24)? Similarly, the result section is very short, and the abbreviations are not explained (e.g., “AggEnt”, “Dur90%” etc) . Is the performance of the classification really above chance? This could be tested with a binomial test.

The figure captions should be expanded. Figures 1-4 do not only show spectrograms but also oscillograms etc. In Figure 5, please explain the abbreviations. Are figures 1 and 2 really needed? Maybe one figure could depict two recordings from Scotland and two form Finland. Similarly, Fig 3 and 4 could be combined. It would also be helpful if Figure 5 was using different colours to represent calls coming from one individual.

The abstract is not really fitting to the rest of the manuscript: the text is framed around the question of conservation, which I think is really interesting. The abstract however suggests that the paper can speak to the question whether black grouses can recognise individuals, or what they can infer from that information (e.g., lines 34f - this sentence would be more suitable in the discussion). It would be better to stay closer to the text in the abstract.

One important point the authors make is that hissing calls are non-vocal sounds. For someone not knowing much about black grouse, this is confusing. it would be helpful to clarify / explain this aspect in more detail.

Lastly, I would suggest moving the first paragraph of the discussion to the introduction. A discussion should start with a short recap of the aim of the study, and then summarise the findings. At the moment, it starts with a discussion of the different call types, which would be more appropriate in the introduction. The motivation for studying individuality in this species is nicely laid out, however it would be helpful to specify how much the population has decreased lately (line 46).
Experimental design: My major concern is with the data collection and how this might have influenced results: the authors recorded hissing calls from males from different display sites to ensuring that they were indeed recording from different individuals. However, although this procedure makes sense to establish the relevant call parameters, it is not clear whether you are measuring individual or location differences. Thus, it is possible that future studies using these parameters cannot differentiate between individuals from the same location. It would thus be necessary to classify individuals from the same location to establish true individuality.
Validity of the findings: In order to really say that the black grouse can be identified by its hissing call, the authors should test whether there was less variation within calls of the same individual than between individuals. In addition, as I have mentioned above, it is not clear whether the findings represent individual or lek differences.
Additional comments: Some minor comments:
-	Throughout the text: should black grouse really be capitalised?
-	Line 44f: consider re-writing as “Although the black grouse is classified as a species of least concern..”
-	Line 47: replace “reasons” with “causes”
-	Line 64: replace “so” with “thus also”
-	Line 87f / 106f: these two sections mentioning ethics and licenses could be combined
-	Line 96: Please explain here what a lek is
-	Line 132: remove the “n” in ”(~n < 1)”
-	Line 143: this information is already provided in the method section
-	Line 144: It would be helpful to have access to the table in the manuscript, as opposed to as supplement
-	Line 160: “but we do not suppose” sounds odd


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: ACOUSTIC INDIVIDUALITY IN THE HISSING CALLS OF THE MALE BLACK GROUSE (LYRURUS TETRIX)
Review round: 1
Reviewer: 2

Output:
Basic reporting: The language was clear, the experiment was put in the context of the literature and figures and data were available. However, there were a number of paragraphs that I was not sure why they were in the manuscript. They were clearly written but seemed to be more examples trying to support a point, though I was often unsure of what point was being supported or why that point was being highlighted in the first place.
Experimental design: Question was clear, why this study was important was clear, and the methods were solid. However, I would have liked to see all of the variables tested and which ones were correlated.
Validity of the findings: The conclusions follow from the findings. The discussion was a bit meandering for me, and I was not sure why some paragraphs were included, but the writing was clear and didn’t overstate the results.
Additional comments: 42-63: I think that this paragraph could be shortened and streamlined a bit, making more general statements about sources of mortality rather than outlining many specific examples.

73-76: here also, it could be shortened, just focusing on the fact that this has shown a lot of promise in other studies but not explaining in detail why and how. Additionally, by including the extra information about the yearling’s song, it undermines the argument that vocal monitoring is a good idea (try focusing on the potential useful possibilities, not on past failures).

77: ‘repose’ is a slightly odd choice of word here, I am not quite sure what is meant by tis sentence. Maybe try thinking of another one.

120-121: what variables? I would like to see these maybe in a table with an explanation for what each variable is, and which ones were highly correlated.

147-152: how were the males that were difficult to classify with accuracy specially patterned? Sometimes theories of individual vocal identification suggest that within close groups/neighbours there is a lot of individual differences, but that this may change as samples from farther away are taken.

155-156: I am a bit confused by this sentence as it starts out with 4 call types, then after 2 suggests that there are 4 more call types?

187-200: while this paragraph has many examples of species in regard to differences in vocalizations, I am not sure what the point of this paragraph is. Please make it a bit clearer in the first few sentences and a last sentence.

213-220: unless this is a specific section included in all PeerJ articles, I think ending without it is stronger.


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: ACOUSTIC INDIVIDUALITY IN THE HISSING CALLS OF THE MALE BLACK GROUSE (LYRURUS TETRIX)
Review round: 2
Reviewer: 1

Output:
Basic reporting: -
Experimental design: My only remaining question refers to the ratio of variables to cases - the authors response does not really addresses my problem, as there are still only 24 cases? Or when did the exclusion happen, after the analysis? To me that is not clear. In addition, it would be good to know more on how / why individuals were excluded - e.g., what does "extreme" mean?
Validity of the findings: -
Additional comments: I am overall happy with the revisions made except see above.
Minor issues I noticed:
-	L 151: include that CV means “coefficient of variation” (maybe like this: “..parameter, we compared the coefficient of variation (CV) within and between individuals.”)
-	L 173: is there a “the” missing?
-	I am not sure I understand table 2. Is the X in the second column indicating significant variables?


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

Input:
Title: ACOUSTIC INDIVIDUALITY IN THE HISSING CALLS OF THE MALE BLACK GROUSE (LYRURUS TETRIX)
Review round: 2
Reviewer: 2

Output:
Basic reporting: The language was clear (barring a few grammatical issues), the experiment was put in the context of the literature and figures and data were available. The intro and discussion were more to the point and straightforward.
Experimental design: Question was clear, why this study was important was clear, and the methods were solid. I was happy to see the inclusion of the table of the variables tested.
Validity of the findings: The conclusions follow from the findings. The discussion was more straightforward, and the writing remained clear and didn’t overstate the results.
Additional comments: 47-48: this sentence makes it sound like this decline is in the past. Maybe something more like “as black grouse continue to decline across its distribution range, . . . “

49-52: this sentence makes it sound like the decline isn’t too worrying, so why then bring it up? Maybe leave out the ‘classified as a species of least concern’ and focus on the decline, or ‘though it is classified as a species of least concern . . . it continues to decline across its range requiring monitoring.’

124-126: how many individuals were there on a lek? Why not look at individuals within leks to make sure they were different, rather than between leks since between leks you can tell different males are present due to site fidelity?

240-251: this sounded a bit like a very short abstract rather than a conclusion. The last 3 sentences were more like a conclusion.


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 MOLECULAR CHARACTERS WHEN MORPHOLOGICAL VARIABILITY HINDERS DIAGNOSABILITY: SYSTEMATICS OF THE MOON JELLYFISH GENUS AURELIA (CNIDARIA: SCYPHOZOA)
Review round: 1
Reviewer: 1

Output:
Basic reporting: This is such a big change for Aurelia, this paper will become a common reference, primarily Figure 10, that is why I feel this figure should be greatly improved:

- please significantly increase the resolution to avoid pixelation, I suggest this be one of the largest figures published.
- code existing, resurrected and new species (i.e. sp. 7 ... ) using a unique symbol to let the reader know these are new or not on the map.
- consider a different palette for colors, for example the in the Gulf of Mexico it is very difficult to tell the dark purple and dark brown points apart as they overlap. Also enabling jitter here should help.
- consider a slightly larger point size on the map (not the legend), points appear quite small relative to the map size.
- consider using the ggplot2 library if it was not used to create the plot
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: This paper is very well written, represents a major change for Aurelia and advances the field for scyphozoan taxonomy. I suggest minor revisions to the map figure before publication.


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

Input:
Title: THE IMPORTANCE OF MOLECULAR CHARACTERS WHEN MORPHOLOGICAL VARIABILITY HINDERS DIAGNOSABILITY: SYSTEMATICS OF THE MOON JELLYFISH GENUS AURELIA (CNIDARIA: SCYPHOZOA)
Review round: 1
Reviewer: 2

Output:
Basic reporting: Lawley and coauthors provide a thorough revision of the iconic jellyfish genus Aurelia. They investigate the morphological and genetic diversity of several samples collected across the world ocean and provide new important data on this taxon. Specifically, they assess the morphological variability of the medusa stage in several species and perform statistical analyses to check for differences among species. At the same time, they produce genetic data based on four DNA regions to reconstruct a phylogentic hypothesis of the genus and to delineate species boundaries. Altogether they show that medusa morphology is not adequate to distinguish Aurelia species and find an alternative way to describe the species, that is the inclusion of genetic characters in the description.
The work is certainly well written and overall all analyses are well done. The stucture of the manuscript, together with figures, tables and supplemental files are adequate and almost ready for publication after minor revisions.
First of all, I suggest to shorten a bit the introduction by merging the first two paragraphs.
Experimental design: The scientific question and the performed morphological and molecular analyses are well explained. All analyses are rigorously done and consistent with the uptodate literature on the research field. I only have some suggestions that, in my opinion, could improve the scientific robustness of the work.
Regarding the morphological analyses I could suggest the authors to try to perform other analyses (such as a discriminant analysis) to assess the importance of each variable in characterising the species and to see if samples are correctly assigned to a given clade/species (a thing that should not expected in most cases, given the presented results).
Regarding molecular analyses, it should be advisable that phylogenetic analyses are performed using parsimony, maximum likelihood, and Bayesian inference for all datasets (single and multi-locus) in order to increase the robustness of the obtained phylogenetic hypotheses.
Moreover, authors could test their species hypotheses using some of the available DNA-based species delimitation techniques (including for instance ASAP, GMYC, PTP, etc).
Finally, I have nothing against naming cryptic species based on genetic data alone if morphology is not useful. Anyway, I believe that a morphological description of the proposed species should be always provided. Therefore, I suggest authors to provide a brief description of all the available life stages for all newly described species.
Validity of the findings: Overall, the work provides important insight into the diversity, evolution, and biogeography of Aurelia species and, in my opinion, fully deserves publication after the minor revisions suggest above.
Additional comments: no other comments


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

Input:
Title: THE IMPORTANCE OF MOLECULAR CHARACTERS WHEN MORPHOLOGICAL VARIABILITY HINDERS DIAGNOSABILITY: SYSTEMATICS OF THE MOON JELLYFISH GENUS AURELIA (CNIDARIA: SCYPHOZOA)
Review round: 1
Reviewer: 3

Output:
Basic reporting: In general, I was able to follow and understand the text. The article follows the standard article structure in general. Raw data files including can be opened and these complemented the manuscript. The results are relevant to the hypotheses and the literature references are sufficient field context provided.
Experimental design: The research is original primary research within the Aims and Scope of the journal. The research question is well defined, relevant, and meaningful and it is stated how it fills an identified knowledge gap.
Validity of the findings: All underlying data have been provided; they are robust, statistically sound, and controlled. Additional details are requested (see general comments)
Additional comments: This research is relevant and fills an important knowledge gap and adds to our knowledge of biodiversity in the world.

In methodology and results should be add the appropriate tables for more details on the specimens.

To detail in methodology how are you present the species delimitation section in the results.

Add a comparative table with genetic and principal morphological features (e.g. morphology of rhopalia), besides the distribution of all species.

Add a section on possible morphological variability between female and male specimens.

Check more comments in the attached file.