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: MOLECULAR DETECTION MAPPING AND ANALYSIS PLATFORM FOR R (MDMAPR) FACILITATING THE STANDARDIZATION, ANALYSIS, VISUALIZATION, AND SHARING OF QPCR DATA AND METADATA
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: It was difficult to adequately test the MDMAP application. Example files worked without issue but would be more of a benefit to test custom datasets and to compare cycle threshold values with supported platforms/software and those employed within MDMAP (th.cyc in the ChipPCR package). More extensive and clear documentation of uploading data, particularly with multiple PCR runs or projects that span a longer time frame would be an improvement.
Validity of the findings: No comments
Additional comments: The following constitutes a review of the scientific article entitled “Molecular Detection Mapping and Analysis Platform (MDMAP) facilitating the standardization, analysis, visualization, and sharing of qPCR data and metadata” for publication consideration in the journal PeerJ. Overall the writing is clear and concise with appropriate and relevant literature cited. The problem and the justification for the submitted work is clearly identified.
This reviewer took the liberty of testing the ShinyApp interface with the example files provided. Linking the web tool through the CRAN community and potentially having access to developed packages that relate to qPCR data reduction and analysis is advantageous by itself. The interface is simple and fairly easy to use. However, currently there are significant limitations in use of the tool and overall clear documentation for use of the MDMAP application is lacking. Many labs do not use the platforms the ShinyApp currently supports, which restricts the reach of this tool to those labs. It’s also difficult to evaluate the algorithm used for determining cycle threshold values with any data other than those created by MIC or Biomeme instrumentation. Although the authors have clearly identified qPCR data standards are urgently needed, it is suggested since testing of this application is difficult with data from any other machine than the three currently supported that the authors provide additional reasoning why MDMAP will reach the standard that other labs should follow. It would also be very helpful to evaluate or compare calculated cycle threshold values from onboard software (regardless of the instrument) to the th.cyc algorithm used in the MDMAP application. In other words, answering the questions how do the algorithms compare and which one(s) are the best. This is critical since MDMAP is specifically reporting and mapping cycle threshold values.
The concept of linking qPCR raw fluorescence values to a standardized cycle threshold value, and then linking that data to project or sample metadata is a worthwhile effort. I imagine further documentation on use of the MDMAP application will be provided in the future although it would have been helpful for a better evaluation of the tool currently. As such, in its current form the manuscript is recommended for publication but will need revision to address the concerns raised above and the specific comments that follow.

Specific comments
Title page; lines 2 and 3: There is another large database effort with the acronym MDMAP through NOAA. If this effort was to become publicly disseminated and searched through web browsers would it be appropriate to alter the acronym slightly to avoid overlap? In fairness, the two efforts are not at all related in focus and should be no issue with leaving as is but a slight change could help with visibility.
Abstract; line 26: I’m ok with leaving this sentence in the abstract, but as written using the word ‘rarely’ implies there are efforts that exist that include associated metadata with qPCR results making MDMAP less novel. Are these efforts referenced appropriately? A couple of examples are eDNAtlas through the US Forest Service and a more recent effort by USGS eNAS. Suggest adding references for these efforts and the main document.
Young, Michael K.; Isaak, Daniel J.; Schwartz, Michael K.; McKelvey, Kevin S.; Nagel, David E.; Franklin, Thomas W.; Greaves, Samuel E.; Dysthe, J. Caleb; Pilgrim, Kristine L.; Chandler, Gwynne L.; Wollrab, Sherry P.; Carim, Kellie J.; Wilcox, Taylor M.; Parkes-Payne, Sharon L.; Horan, Dona L. 2018. Species occurrence data from the aquatic eDNAtlas database. Fort Collins, CO: Forest Service Research Data Archive. Updated 08 November 2019. https://doi.org/10.2737/RDS-2018-0010
Abstract; line 33: The effort is not just eDNA focused with regards to species distribution, but includes qPCR results from other applications such as gene expression studies, pathogen detection, etc, is it not? This is perhaps where the novelty of MDMAP resides. Can the authors spell out better exactly what types of studies MDMAP supports in the abstract? What areas of molecular diagnostics can MDMAP facilitate sharing of data?
Introduction; line 74: Seems a strange way to identify ‘samples’ as ‘qPCR samples’. Samples can be water samples, soil samples, tissue samples, etc. Considering rewording.
Introduction; line 84 – 87: Poor sentence structure, reword. Here is a suggestion, “As a consequence, the extended use of qPCR in environmental DNA (eDNA) surveys is producing a large amount of qPCR data (e.g., the qPCR raw fluorescence outputs) and associated metadata.”
Introduction; line 90: ‘bioinformatics tools’…Can the authors provide specific examples?
Introduction; line 90 – 91: ‘with few tools’. If there are a few, what are they? eDNAtlas? Other?
Introduction; line 101: What specific qPCR applications will be supported? Only eDNA? Other applications? In addition, it would be beneficial for the authors to expand on how this tool will be deployed…perhaps most appropriately in the discussion section.
Introduction; line 102: Hyphenate when open-source is used as an adjective.
Methods and Results; line 108: MDMAP acronym may overlap through searching common web browsers with NOAA’s Marine Debris Monitoring and Assessment Project (MDMAP). Author(s) may consider another acronym for visibility and easier accessibility.
Methods and Results; line 119 – 120: This is a fairly limited list of thermalcyclers and associated software packages. I can see the next sentence references the possibility of extending to other systems, but this is still a very limited list and in the short term limits the utility to only those labs that have these instruments. What time frame or how extensive of an effort will be required to expand support to other systems? If not in the discussion, the authors should comment on this.
Methods and Results; line 122: ‘qPCR well names’. This is adequate for individual qPCR runs, but what happens for subsequent runs or repeated runs where well names are redundant? Is there an underlying database schema that retains individual run information, or is this tool useful for only getting the raw qPCR fluorescence data in a format to be mapped, visualized, and shared one qPCR run at a time?
Methods and Results; line 125: Pre-set implies the user has some control over this. Does that happen in the qPCR software prior to raw data download to MDMAP or is there user control within the ShinyApp for threshold? Threshold varies considerably in the Example Files in the Data File Preparation page of the app. Can the authors expand on how much control users have over the threshold setting and exactly where that may occur? This is critical since the ChipPCR package uses threshold to calculate Ct values via the function th.cyc()
Methods and Results; line 139: Commend the authors for thinking ahead here as inevitably there will be other tools such as MDMAP that have been or will be developed. Standardization of records and record labels will make sharing of data across different platforms more streamlined. This is certainly a strength of this effort.
Methods and Results; line 151: Not the target species…rather…the target species DNA
Methods and Results; line 152 – 153: ‘default cycle threshold value in MDMAP is adjustable’. Another critical point for eDNA studies since different qPCR markers will carry different levels of PCR efficiency and corresponding sensitivity. Can the authors explain why this parameter must be adjusted in the R code itself, and was not included as an adjustable parameter in the MDMAP ShinyApp interface?
Methods and Results; line 162: change ‘in the field’ to ‘in a given sample’.
Methods and Results; line 163: change ‘divides’ to categorizes’.
Methods and Results; line 168 – 170: The selected default qPCR intensity settings are extremely wide. Most eDNA Ct values will likely fall at or above Ct 30, rarely below that unless sampling where the target species is at a very high density (such as epidemiological studies where bacterial/viral loads are extremely high). It’s great that the authors provided user control over the intensity settings, but is there any guidance provided (or can it be provided) on the ShinyApp for some considerations on real world examples for the range of values that should be expected for a given qPCR application?
Discussion; line 184: ‘presence or absence’. Is it more appropriate to say ‘relative Ct values’ when referring to qPCR signal intensities. Presence or absence only refers to whatever the set Ct cutoff value is, not the range of values.
Discussion; line 185 – 186: How do multiple projects or studies get merged and mapped together? I’m thinking along the lines of multi-year projects where the same areas are sampled repeatedly. Can this be done and can the authors expand on that topic a bit more?
Discussion; line 198 – 201: Although the summary of R packages and CRAN is nice, it’s not relevant to this discussion in my view. More of an advertisement for R. I think the previous sentence provides ample information to document the footprint of R and the extensive set of resources and user groups it provides. This sentence can be removed.
Discussion; line 209: remove ‘associated’.
Discussion; line 231 – 233: The effort to incorporate color-coded signal intensities is a nice addition, but arguably subjective in nature. The example given (detection of endangered species) may give all detections that would be considered ‘weak’ to most eDNA practitioners. It may be more useful in some circumstances to ‘omit’ the color-coded signal intensity mapping and instead map points with associated Ct values instead. Have the authors considered this alternative as a user option in MDMAP?
Discussion; line 234: ‘temporal relationships’. It’s not clear where the merging of multiple raw data sets representing qPCR runs over time occurs. Does this happen prior to upload on MDMAP? Can the authors provide more context on what a user would have to do to format data for this type of upload and mapping?
Discussion; line 247: change ‘or few’ to ‘or a few’.
Discussion; line 260: change ‘provides this framework’ to ‘provides a framework’.
Discussion; line 260: Since there are others developed, MDMAP isn’t the only one. However, it would be useful to provide context of how MDMAP compares or contrasts to Holland et al. 2003 and Konig et al. 2019.
Discussion; line 269 and 271: hyphenate ‘open-source’.
Discussion; line 301 – 303: Certainly a nice feature, but can users also filter by qPCR marker? This could be important when it is known one marker is more sensitive than others. Is markerID retained as a field in the columnar data?
Discussion; in general: The authors have not addressed anywhere in the paper how MDMAP would handle a qPCR marker that is not species-specific. For instance, many markers are genus-specific (e.g. Dreissenid mussels) or may detect multiple species within a genus but not all species within a genus. How are those circumstances handled within MDMAP?
Discussion; line 313 – 316: How much effort will it take to incorporate other platforms since many labs do not use Biomeme or MIC qPCR platforms? Please provide some insight into the difficulty or timeframe it may take for this to happen.
Discussion; line 318 – 320: Suggest rewording one of the two sentences that start with ‘For example’. Redundant.
Discussion; line 322: A descriptor is missing here. MDMAP’s “…”?
Discussion; line 322 – 324: This entire sentence needs rewording. It is not clear what the authors are trying to say.
Discussion; line 328 – 329: Suggest ending sentence with a ‘.’ after conclusions, removing ‘and’, and starting a new sentence with ‘Conclusions based on absence…’. Run on sentence currently.
Discussion; line 331 – 333: Nice discussion point. Authors may consider mentioning occupancy modelling of eDNA data. One potential integration point of MDMAP with an existing R package for analysis of eDNA data would be ‘eDNAOccupancy’. See Dorazio and Erickson 2017.
Conclusion; line 363 – 366: Sentence needs rewriting. Run on with too many ‘ands’ along with strangely worded in the phrase ‘MDMAP is addressing a critical need in addressing…


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: ON THE GENUS MESOPONTONIA BRUCE, 1967 (CRUSTACEA: DECAPODA: PALAEMONIDAE) IN KOREA, WITH THE DESCRIPTION OF A NEW SPECIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article should be re-evaluated for professional English usage. Sentences are long and complex, making understanding of the context difficult. The unit of each quantity should always be informed.
Experimental design: No comment
Validity of the findings: No comment.
Additional comments: Morphological and genetic results are convining to prove that the creature is a new species.
However, the language usage is still needed to be re-checked for complex and non-informative sentences.


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: ON THE GENUS MESOPONTONIA BRUCE, 1967 (CRUSTACEA: DECAPODA: PALAEMONIDAE) IN KOREA, WITH THE DESCRIPTION OF A NEW SPECIES
Review round: 1
Reviewer: 2

Output:
Basic reporting: This manuscript describes a new species and a new record of Mesopontonia shrimps in Jeju island, Korea. The manuscript is largely taxonomic based, contains only one new species and new records. Readers of Peer J include colleagues from wide ranges of fields. One of the attractive point of this article is these shrimps is from mesophotic coral reefs in Korea, which is rather unknown habitats and with understudied diversity. I think if it is to be accepted in Peer J, it should be value-added by mentioning these species are from mesophotic coral reefs, mesophotic zone coral reef ecology in Jeju and with some more discussion on the reproductive period of Mesopontonia verrucimanus in Jeju at the end of discussion.
Experimental design: The paper is taxonomic based, no comments on experimental design.
Validity of the findings: see my comments for author below
Additional comments: This manuscript describes a new species and a new record of Mesopontonia shrimps in Jeju island, Korea. The manuscript is largely taxonomic based, contains only one new species and new records. Readers of Peer J include colleagues from wide ranges of fields. One of the attractive point of this article is these shrimps is from mesophotic coral reefs in Korea, which is rather unknown habitats and with understudied diversity. I think if it is to be accepted in Peer J, it should be value-added by mentioning these species are from mesophotic coral reefs, mesophotic zone coral reef ecology in Jeju and with some more discussion on the reproductive period of Mesopontonia verrucimanus in Jeju at the end of discussion. The MS will need revisions according to my comments below. I am happy to read the revised manuscript again.

Specific comments are:

1)	The name “Jejudo Island” – The authors can consider to use the name Jeju Island. Jeju Island appears to be more commonly found in the internet and scientific literatures. The word ‘do’ in Jejudo already carry the meaning of ‘Island’ in Korean language, so it is appropriate to name it as Jeju Island.

2)	Lines 70-72, the authors stated “The sea area around the island is largely influenced by the warm, saline Tsushima Warm Current, a branch of the Kuroshio Current, flowing northeastward through the Korea Strait from the East China Sea (Lie et al. 2000).” The authors can modify this sentence. In summer, Tsushima current is mixed with low-salinity, high-turbidity waters from the Yangtze River to influence the waters in Jeju Island. In winter, the Yangtze River discharge reduced and result in higher salinity (Rebstock and Kang, 2003; Lim et al. 2019). Lim et al. (2019) which contains plots of salinity in summer and winter and also surface temperature in Munseom. Also see Rebstock and Kang, 2003 for currents (hyperlinks for literatures attached below for your references). These references should be cited in text.

3)	Lines 72-74, the authors stated “Munseom Islet (Fig. 1C) is located off the south coast of the main island, and consists of volcanic rocks covered with rich invertebrate communities” I would suggest citing three references as “Munseom Islet (Fig. 1C) is located off the south coast of the main island, and consists of volcanic rocks covered with rich invertebrate communities (Cho et al. 2014, Lutaenko et al. 2019; Lee et al. 2019).” Cho et al. (2014) contains a survey of diversity of invertebrates in Munseom. Lutaenko reported at least five new species of bivalves in Jeju. Even a new species of brittle star is recently identified from Munseom suggesting its high invertebrate diversity here. (hyperlinks for literatures attached below for your references)

4)	Starting from line 93, I would suggest the authors use a few sentences to describe a general diversity of corals, sponges and soft coral species in the mesophotic environment they dived in Jeju. Diversity and ecology of Mesophotic environment received very little attention. Even the book “Mesophotic Coral Ecosystems” (https://www.springer.com/gp/book/9783319927343) contains chapters of mesophotic coral communities in Okinawa, Japan and Taiwan but without Korea. So, having some information about the mesophotic zone and with some photos of the habitat if possible can enhance this article not solely interested by specialist taxonomist.

5)	Figure 9 – 11 illustrate the morphological part of the new species. I would suggest in these figures, use arrows to indicate diagnostic part which are unique for this species. In the remarks of M. kimwoni sp. nov, the authors stated how this species is different from other described closely related species. Since this is a submission to Peer J, readers of Peer J is not specialist in specific taxonomic group. I would suggest the authors to make an additional figure, with some diagrammatic line drawings for other species and show how the new species can be distinguished from others. So, non-specialists can also follow the identifications.

6)	Lines 144-185, I can see authors has described whether females are ovigerous or not from the specimens of Mesopontonia verrucimanus collected in Munseom from various months in 2018 and 2019. I would suggest to plot a simple horizontal bar chart covering the year 2018 and 2019, blacken the bars in those months when the females are ovigerous. This can show the occurrence of ovigerous females in summer months but not winter months. This showed that the reproductive cycle of shrimps in mesophotic zone are seasonal. Comparisons can also be made to subtidal bivalves in Munseom (Fig. 10 in Lim et al. 2019). Subtidal communities in Jeju have mature gonads in June to August. This period overlapps a portion with period of ovigerous Mesopontonia verrucimanus, but M. verrucimanus extend its reproductive season to September, slightly longer than subtidal bivalves. An additional paragraph in the discussion can be made to discuss the reproductive cycle of females of M. verricimanus and compared the pattern with subtidal bivalves in Jeju.

References

Cho et al. 2014 https://www.researchgate.net/publication/262880572_A_study_on_the_biodiversity_of_benthic_invertebrates_in_the_waters_of_Seogwipo_Jeju_Island_Korea

Lutaenko et al. 2019
https://www.researchgate.net/publication/334230937_Lutaenko_KA_Noseworthy_RG_Choi_K-S_Marine_bivalve_mollusks_of_Jeju_Island_Korea_Part_1_The_Korean_Journal_of_Malacology_2019_v_35_N_2_pp_149-238

Lim et al. 2019
http://zoolstud.sinica.edu.tw/Journals/58/58-29.pdf

Lee et al. 2019
http://zoolstud.sinica.edu.tw/Journals/58/58-08.pdf

Rebstock and Kang, 2003
https://www.sciencedirect.com/science/article/abs/pii/S0079661103001769


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: ON THE GENUS MESOPONTONIA BRUCE, 1967 (CRUSTACEA: DECAPODA: PALAEMONIDAE) IN KOREA, WITH THE DESCRIPTION OF A NEW SPECIES
Review round: 1
Reviewer: 3

Output:
Basic reporting: English in this manuscript should be edited by the expert in order not to make any confusion in the sentences.
Literature references, figures, and tables are suitable for publication.
Experimental design: Mitogenome sequencing technique is well established in numerous publications and they used the typical methods. Therefore, there is nothing to commend about experimental design.
Validity of the findings: Reporting two additional mitogenome sequences in the Dendrobranchiata is the main topic in this manuscript. They found two mitogenome sequences are the same as the previous studies in the overall structures, gene organization, and phylogenetic relationship. therefore there is few novel findings in the manuscript except for mitogenome sequences. If the policy of this manuscript is OK, overall writing and structures for this manuscript are typically acceptable.
Additional comments: Reporting two additional mitogenome sequences in the Dendrobranchiata is the main topic in this manuscript. The authors found two mitogenome sequences are the same as the previous studies in the overall structures, gene organization, and phylogenetic relationship. Therefore there are few novel findings in the manuscript except for adding mitogenome sequences. If the policy in this manuscript accepts this kind of manuscript, overall writing and structures for this manuscript are typically acceptable. Their contribution is the addition of two mitogenome sequences in the taxa.


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: ON THE GENUS MESOPONTONIA BRUCE, 1967 (CRUSTACEA: DECAPODA: PALAEMONIDAE) IN KOREA, WITH THE DESCRIPTION OF A NEW SPECIES
Review round: 1
Reviewer: 4

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: Representatives of the deep-water pontoniine shrimp genus Mespontonia are quite rare for scientists and any records of these shrimps are extremely interesting. However, this is also a problem for describing new species. All previously described species are extremely morphoogically close, while, that is more important, intraspecific variability of the morphology are absent for most species. In this regard, it is difficult to determine any stable and important diagnostic morphological features within the genus.
This presented article describes well describe the found shrimpss and the morphological differences between studied species. In addition, genetic differences are shown.
At the same time, the genus Mesopontonia currently includes 6 valid species, which, like most caridean species in the Indo-West Pacific, can be found in any part of this zoogeographical region. Morphological differences from other species in the article are described and discussed very poorly and only in general features (like length\width ratios nd measurements). Moreover, some species (for example, M. brevicarpus, which seems to be most morphologically close to the newly described species) were initially poorly described (see Li, 2006), and many morphological features have not been specified ince the original description. Most of species within the genus need careful morphological re-description. Also, the presented genetic data and the absence of such data for other species of the genus do not allow to conclude that authors are dealing with different biological species.
In this regard, I cannot unfortunately conclude that the described species is really new to science. For me, the morphological features of the species from other species of the genus, for example, M. brevicarpus, are not obvious, and not confirmed in any way. The discussed morphological structures can be found in large/small individuals and no previous studies have indicated them as diagnostic and sufficient to identify the new species.
In the case of genus Mesopontonia, the description a new species need the complete revision of the genus (better, using molecular data), which is very likely to lead its significant reduction. However, at least a revision of the morphological features of all the described 6 species is extremely important for the study of the diversity of the genus.

Final decision - the article cannot be published with a description of the new species (as presented), since its separation is not confirmed by either morphological or genetic data.
Additional comments: Representatives of the deep-water pontoniine shrimp genus Mespontonia are quite rare for scientists and any records of these shrimps are extremely interesting. However, this is also a problem for describing new species. All previously described species are extremely morphoogically close, while, that is more important, intraspecific variability of the morphology are absent for most species. In this regard, it is difficult to determine any stable and important diagnostic morphological features within the genus.
This presented article describes well describe the found shrimpss and the morphological differences between studied species. In addition, genetic differences are shown.
At the same time, the genus Mesopontonia currently includes 6 valid species, which, like most caridean species in the Indo-West Pacific, can be found in any part of this zoogeographical region. Morphological differences from other species in the article are described and discussed very poorly and only in general features (like length\width ratios nd measurements). Moreover, some species (for example, M. brevicarpus, which seems to be most morphologically close to the newly described species) were initially poorly described (see Li, 2006), and many morphological features have not been specified ince the original description. Most of species within the genus need careful morphological re-description. Also, the presented genetic data and the absence of such data for other species of the genus do not allow to conclude that authors are dealing with different biological species.
In this regard, I cannot unfortunately conclude that the described species is really new to science. For me, the morphological features of the species from other species of the genus, for example, M. brevicarpus, are not obvious, and not confirmed in any way. The discussed morphological structures can be found in large/small individuals and no previous studies have indicated them as diagnostic and sufficient to identify the new species.
In the case of genus Mesopontonia, the description a new species need the complete revision of the genus (better, using molecular data), which is very likely to lead its significant reduction. However, at least a revision of the morphological features of all the described 6 species is extremely important for the study of the diversity of the genus.

Final decision - the article cannot be published with a description of the new species (as presented), since its separation is not confirmed by either morphological or genetic data.


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: ON THE GENUS MESOPONTONIA BRUCE, 1967 (CRUSTACEA: DECAPODA: PALAEMONIDAE) IN KOREA, WITH THE DESCRIPTION OF A NEW SPECIES
Review round: 2
Reviewer: 1

Output:
Basic reporting: The authors has addressed major part of the comments and the MS can be accepted. Of course I agree the illustration is at the professional level. Whether the authors is encouraged to add in more ecological and illustration for non-specialists/beginner to understand is really depends the editor's decision on the scope of PeerJ - a really specialist taxonomy journal or a biodiversity, taxonomy and ecology journal for both specialists and general readers.
Experimental design: Addressed
Validity of the findings: Addressed
Additional comments: The authors has addressed major part of the comments and the MS can be accepted. Of course I agree the illustration is at the professional level. Whether the authors is encouraged to add in more ecological and illustration for non-specialists/beginner to understand is really depends the editor's decision on the scope of PeerJ - a really specialist taxonomy journal or a biodiversity, taxonomy and ecology journal for both specialists and general readers.


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 PAST CENTURY OF CORAL BLEACHING IN THE SAUDI ARABIAN CENTRAL RED SEA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript uses stress bands from massive Porites cores in the central Red Sea, along with climatology data, to identify past bleaching events in the area of the past 100+ years. The study complements more recent in situ observations of coral bleaching from the past ~ 20 years, and despite identifying possible undocumented bleaching events prior to the 1980s, concludes that the frequency and severity of bleaching events has increased in recent years.

The manuscript is well-written and I feel is suitable for publication providing some minor comments (highlighted below under ‘general comments’) are addressed – these include some comments that are merely suggestions to be addressed at the author’s discretion.

Overall, I think the manuscript is straightforward and will be a solid contribution to the field – I commend the author for their work.
Experimental design: The overall rational and design of the study are clear and sufficiently detailed.

While the number of cores is limited, I recognise the difficulty and environmental impact of collecting a large number of cores. Additionally, the author seems to have used an appropriate statistical approach to account for this and, generally, interprets the results with this limitation in consideration – though there are a one or two sections, detailed below, where I think a more conservative interpretation may be more appropriate.
Validity of the findings: While I am not familiar with the technical aspects of using stress bands on coral cores to indentify past bleaching events, the author has previously published peer-reviewed work using this approach and cites past studies in support of the methodology. I therefore see little reason to doubt the validity of the approach unless another expert reviewer expresses concern.
Additional comments: Line 15: Do you mean 20th century?

Lines 31-32: It is my understanding that the term ‘zooxanthellae’ is colloquial and no longer appropriate. I would suggest removing it on line 31 and changing it to ‘endosymbiont photosystem’, or something similar, on the following line.

Line 61: ‘a’ hypothesis

Line 68: There is a paper by Raitsos et al. (2011) in Geophysical Research Letters that reports a considerable increase in temperature in the region since the mid-1990s – it may be relevant to refer to it here or elsewhere in the paper.

Line 75: not sure the ‘currently’ is necessary.

Line 77-79: I think you should state here that you also analyse and compare long-term climatology datasets that include temperature and wind data - you don’t only use the coral cores to reconstruct the bleaching events.

Line 84 and throughout: While I understand, and agree with, the benefit of using the active voice, I do think the use of ‘my’ often is not appropriate and could be replaced with ‘the’. Notably, on line 252, you say ‘my bleaching history’ when referring to the bleaching history reconstructed in the study – which I think is incorrect.

Line 86: I would suggest stating the total number of cores collected outside of Abu Shosha.

Line 146: When you say ‘ranged in age’ do you mean that they dated as far back as the years stated?

Line 148-150: I think it would be helpful to say how many of the 11 cores did or didn’t have bands here? Just to get an idea of the overall proportion of cores/colonies that did bleach.

Same for the non-Abu Shosha cores below (would be good to state many cores were taken in total and how many experienced bleaching).

Line 162: How many cores were these three bands found on?

Line 205-206: Did this analysis yield a p-value regarding the significance (or non-significance) of these correlations?

Line 249: I think this should toned down further considering the meagre evidence/data available - it leaves open the possibility that a bleaching event occurred in this year. There really isn’t any evidence to support the occurrence of a severe bleaching event.

Line 300: You allude to it somewhat here, but I think a clear statement is missing in the discussion that indicates that the recorded stress bands may have been caused by something other than bleaching (even maybe disease or something else?), which may explain why you found stress bands on one or two colonies in years despite no evidence of high temperature/light or low wind in those years.

Line 325-327: This really is a personal/stylistic thing, but I don’t personally agree with the approach to this section. I think the author could do without this statement and simply discuss the timeline of bleaching over the last century chronologically without separating it by year.

E.g. ‘In 1931, SSTs appear to have…’

This is very much up to the discretion of the author, however.

Line 328: Shouldn’t it be ‘SSTs appear’ rather than ‘SST appears’? There was more than one recording of SST this year, no?

Figures: The figure legend for figure 3 could be written more formally – I would suggest something like ‘CT scans of coral skeletal cores collected outside of Abu Shosha. Refer to figure 2 legend for a full description of the figure.’


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 PAST CENTURY OF CORAL BLEACHING IN THE SAUDI ARABIAN CENTRAL RED SEA
Review round: 1
Reviewer: 2

Output:
Basic reporting: This is a well-written manuscript based on 22 Porites cores drilled out of long lived corals in the central Red Sea. This is a fortune when considering the amount of data recorded in these cores. I was excited and very curious reading the title of the ms and the abstract because the potential is huge. I was a bit disappointed when discovering that the bleaching record of the past century is not so straightforward and that the use of these cores was limited to tracking stress bands rather than supporting it with a stable isotopic work and densitometry. As is, it leaves many open questions and of course, the cores can be used for further analyses.

Yet, the ms is informative and important for anyone working in this region.

The title is a bit misleading because in fact we learn that beyond recent, observed bleaching events (1998, 2010, 2015) stress bands may not be the best proxy or, maybe there was only a minor, local bleaching event with only a few cores recording stress. so little do we learn about the bleaching events in the last century.
proposed title: Can stress bands reliably report bleaching events in the Red Sea?
Anyway, I enjoyed reading it.
Experimental design: No issues with the sampling procedure and analyses.

L148- the author state the number of annual bands counted. Impressive but why is is this important or useful?
The Porites species issue: how many/which species were likely included in the study and what is known on the species sensitivity to thermal stress?
Is it possible to present the densitometric profile along the core and linear extension? I find it very interesting and I suppose the data for this exists?
I'm not entirely sure I understood the need in calculating the probability of finding stress bands. maybe elaborate further on this.
Good job comparing the different sources of temperature records for the region.
Validity of the findings: Findings are straightforward. Well presented and analyzed.
Additional comments: As mentioned above, I like the study but would have liked to see more analyses to decipher the source of stress (temp, nutrients, light and interactions between these parameters).
Consider looking at cores (images in papers) from other regions in the Red Sea, can you detect some annual bands that might be stress bands? in some cases (Klein et al. 1997) these have also the isotopic signature to support thermal stress.
Porties is considered thermally resilient and as such may be insensitive to high DHW. I think it is worth discussing it.
is it possible that under severe stressful conditions, the more sensitive porites colony will miss a band? not calcify/grow at all? if so, maybe some "missing stress bands" are the result of 0 growth?


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: FLOWER STRUCTURE AND DEVELOPMENT IN VIETNAMESE SCIAPHILA (TRIURIDACEAE: PANDANALES): REFINED KNOWLEDGE OF THE MORPHOLOGICAL MISFIT FAMILY AND IMPLICATIONS FOR TAXONOMY
Review round: 1
Reviewer: 1

Output:
Basic reporting: This is an excellent paper that merits publication with little revision. It provides descriptions of developmental morphology in two genera of the mycoheterotrophic family Triuridaceae. This unusual family is of broad general interest but is highly challenging to collect and examine, and hence is relatively poorly-known. I particularly like the attention to detail, such as the record of a “globose knob” (which appears glandular) at the tips of the tepals in one unusual specimen of S. nana.

The paper is well presented with high-quality images. There are currently 30 figures, each containing few images, all of them essential for the paper. The logistics of embedding this number of figures into a relatively short text might be problematic, so if possible I would suggest combining some of them into fewer but larger figures (but not essential).

In general, the english is good, but there are a few typos and other grammatical issues that I have marked separately on an uploaded pdf file.
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Flowers versus inflorescences: The question regarding the evolutionary derivation and homologies of the reproductive units of Triuridaceae (Introduction, lines 50-53) is largely a matter of interpretation and has neither been proved nor refuted (lines 53-54). Rudall, Alves & Sajo, (2016) used the term “flower”, but pointed out that the homeosis theory (Vergara-Silva et al., 2003; Ambrose et al., 2006; Álvarez-Buylla et al., 2010; etc) was applied only to the inside-out flower of Lacandonia. The homeosis theory therefore does not address the question whether the Triuridaceae flower is evolutionarily derived from a flower or an inflorescence, because homeosis (heterotopy) in Lacandonia occurred well after the family Triuridaceae evolved (see Fig. 13 in Rudall, Alves & Sajo, 2016).

Filamentous structures: The term “morphological novelty” does not necessarily apply to organs sui generis (lines 57-58); Rudall (2008) applied this term to several unusual features in triurids, including the presence of carpel fascicles, centrifugal carpel inception, paired carpel arrangement, unusual filamentous structures in atypical positions, and the remarkable inside-out flowers of Lacandonia. The fact that these unusual structures are associated with different organs in different triurids is remarkable (as nicely highlighted in this paper).

Tribal classification: There is currently no mention of the existing tribal classification within Triuridaceae. I would suggest at least mentioning that Sciaphila belongs to the tribe Sciaphileae Miers (five genera: Merckx et al. 2013).

Generic limits: As the authors state, it is entirely reasonable to continue to recognise Sciaphila and Seychellaria as distinct from each other pending further data, as the analysis of Mennes et al. (2013) did not include all species and encompassed some long branches. Mennes et al. (2013) discussed this problem, and noted the need for further taxonomic work in this tribe.

Similarity with Sagittaria (line 600): The observations of similar gynoecium and carpel development to Sagittaria (Alismataceae) and the "embedding" of carpels within the receptacle are interesting, because extragynoecial fertilization (via the receptacle) has been reported in both Triuridaceae (Lacandonia) and Sagittaria (for discussion see Rudall et al. 2016).

Other potentially relevant papers on Triuridaceae: It seems surprising that Hemsley (1907) is not cited for his comments on Sciaphila and Seychellaria. Rudall et al. (2016) noted his statement that some specimens of Sciaphila are ``quasi-hermaphrodite'' and often irregular
as to the number and location of the floral parts. It might also be interesting to compare floral orientation and variation in an African triurid, Kupea, which has monosymmetric flowers and considerable variation in organ number (Rudall et al. 2007).
[Hemsley 1907 Annals of Botany 21: 71-77. Rudall et al. 2007, Kew Bulletin 62: 282–292).


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: FLOWER STRUCTURE AND DEVELOPMENT IN VIETNAMESE SCIAPHILA (TRIURIDACEAE: PANDANALES): REFINED KNOWLEDGE OF THE MORPHOLOGICAL MISFIT FAMILY AND IMPLICATIONS FOR TAXONOMY
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article reports on flower structure and development in poorly studied genus Sciaphila using scanning electron microscopy. Investigation of flower structure and development is sometimes very challenging, especially in plants with very small flowers, as Sciaphila is. Furthermore, Sciaphila plants are achlorophyllous, thus their vegetative parts are reduced making flowers and fruits almost only organs useful for assessment of morphological difference between individual species. As many structures in Sciaphila flowers have been viewed differently by various authors, this study could have significant impact in taxonomy of the genus.
As I am not a native speaker, I do not comment on English. As far as I can judge, the paper is written clearly and professionally. Its structure and content conform to professional standards and the paper offers an insightful introduction to the studied problematics.
Experimental design: The paper presents original primary research. Research questions are clearly stated covering gaps in current knowledge. Methods are described appropriately. Authors used scanning electron microscopy, which was essential to investigate satisfactorily the floral development of Sciaphila flowers. Results are presented as a series of commented SEM photographs, which are of high technical quality. Although all images are relevant to the content of the article, I would welcome descriptions of some SEM photographs to be more detailed. E.g., in Fig 30B no details are given; see also note attached to Fig. 18. While style (its position etc.) is frequently discussed in the text, it is never labelled in presented photographs.
Validity of the findings: The results of the study contribute significantly to the knowledge of floral development and flower structure in the genus Sciaphila. The findings are undoubtedly valid, although stronger results would be obtained if more species (representing a wider range of morphological variation within the genus) were included in the study. However, I agree with all the conclusions stated by the authors.
Additional comments: My only concern is the taxonomical identity of plants used in the study and named as Sciaphila nana. This species was described from Java and the original description did not include male plants, which are usually essential for proper delimitation of Sciaphila species. Therefore, Sciaphila nana is an incompletely known species and naming various populations across Southeast and East Asia by this name is not desirable. This paper is an example of ambiguity connected with this name. Authors used two morphologically clearly different populations named as S. nana and speculated if they even can represent a single species. I would recommend avoiding using this name, or at least use it in the form of Sciaphila cf. nana and explain why the plants are named by this name.


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: COMPUTERIZED MONITORING OF COVID-19 TRIALS, STUDIES AND REGISTRIES IN CLINICALTRIALS.GOV REGISTRY
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper "Computerized monitoring of COVID-19 trials, studies
and registries in ClinicalTrials.gov registry" by Mayer and Huser summarizes and describes the distribution of more than 1000 COVID-19 studies and divides these studies into several subgroups (e.g. by study design, Country, intervention type, etc). During this study, authors laboriously assembled all available data and joined it in the github repository. However, access to the data is obstructed by poor code commenting.
Experimental design: The paper fully describes and classifies available COVID-19 studies. However, there are some questions and advice for authors to structures the work and make in to be much more profitable than simple study review:
-The comment on github "(will be updated frequently)" status is not enough for treating the study to be completed;
-Readme file lack of description in the 'code' field;
-The code file 'covid2_cm.R' should contain more commentaries.
-There should be an obviously called example (e.g. example.R) file to pull data from the repository;
-Also short quickstart tutorial should be helpful;
-In my opinion, the results section should start with an overall database description;
-The structure of the database is definitely lack study scheme and a listing of available data described with column definitions;
Validity of the findings: The approach designed by the authors is potentially groundbreaking since there are many laboratories concentrated on the COVID-19 problem and the way to quickly determine the specificity of the hypothesis is highly required. But to become so, the paper needs to be reworked to highlight it's perks. The available data is messy and hard-to-understand for someone who did not participate in the study.
Additional comments: Instead of data classification, it is probably better to concentrate efforts on the description of the database authors assembled, which will result in the excellent paper many researchers will find very useful.


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

Input:
Title: COMPUTERIZED MONITORING OF COVID-19 TRIALS, STUDIES AND REGISTRIES IN CLINICALTRIALS.GOV REGISTRY
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript review is titled Computerized monitoring of COVID-19 trials, studies, and registries in ClinicalTrials.gov registry, submitted to PeerJ for review. The manuscript conforms to the expectations of the PeerJ guidelines, and the needs of the scientific community, especially during the time of this pandemic.

The authors of the manuscript have done an excellent job summarizing the context of the use of automation and informatics for repositories like Clinicaltrials.Gov (CTG) using COVID-19 and the ability to repurpose the methodology and design for other disease conditions. Appreciate the high quality and intensive research effort conducted by the authors. The content is very good but could benefit from some restructuring.

The level of interest from a methodology perspective is on par, but would greatly benefit from a detailed description of the need for data automation & informatics, specifically in the introduction/background section. Example https://www.ncbi.nlm.nih.gov/pmc/articles/PMC7216865/
Experimental design: The manuscript is within the scope of PeerJ’s area of medical sciences. The study design and methodology is well defined. The author described well the scope limitation and formulated well-defined methods for future studies. Additional comments in the general comment section.
Validity of the findings: The search strategy is very well written and has supporting raw data and codes available.
In the discussion section, the authors have made a good effort in categorizing the two facets to discussion journalist and data science perspective. The data science perspective lacks the description of the need for informatics. Although the authors mention the role of manual vs automation from past studies, would be helpful to acknowledge how automation of such datasets influences research in the area of public health emergencies, etc.
Additional comments: As a general comment, this manuscript is important and needs to be published. It is outlined like a methods manuscript and how those could be applied to specific studies, with appropriate analysis.

Major comments:
Row 78: Introduction - you suggest the goal of the study is to demonstrate automated and research informatics methods to analyze a set of closely related studies. I would suggest broadening this to highlight the application of general statistical principles. This would support the discussion in sections methods and results.

Recommendation on restructuring: The draft switches between what a reader would expect from row 108 2.1 Analyzed study section, between analysis of studies based on (1) interventional trials, (2) observational (3) registry studies, to section 2.2 Analysis, 2.3 Intervention Trials 2.4 Observational studies and registries. From a readership, perspective recommends having a section of 2.3 Study types and then sub-sections for interventional and, observational and registries.

Minor comments:
Row 65: recommend to add: what this kind of analysis will help inform? Just a broad general characterization such as clinical guidelines development, etc.

Row 82: COVID-19 clinical studiess , spelling error

Row 110: (3) Recommend modifying registry studies to registry-based studies

Row 113: ‘,’ to be removed before We

For figure 2, a higher resolution image might be helpful.


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: COMPUTERIZED MONITORING OF COVID-19 TRIALS, STUDIES AND REGISTRIES IN CLINICALTRIALS.GOV REGISTRY
Review round: 2
Reviewer: 1

Output:
Basic reporting: The paper "Computerized monitoring of COVID-19 trials, studies
and registries in ClinicalTrials.gov registry" by Mayer and Huser was greatly improved after revision and consider most of the questions reviewers asked.
Experimental design: 1. The discussion section of the manuscript was altered and revised with the huge updates in the Readme file, which is now much more clear than before the review;
2. regCovid_code_for_analysis.R and regCovid_example.R code now joins the required code for downloading and filtering the data from the AACT database;
3. The authors added a file called regCovid_example.R which store an obvious and well-commented example of the code;
4. The authors added regCovid_tutorial.md that contains manual for running the code along with HTML explaining content of the GitHub directory;
Validity of the findings: Even since authors greatly modified the results sections, it is still lack of the newly-added files e.g. regCOVID_data_file_descript.html, regCovid_tutorial.md and regCovid_example.R with links and short descriptions of the file content.
Additional comments: A huge perk to the understanding of the db structure should be considered a quick-start guide located at regCovid_tutorial.md, HTML with file descriptions located at https://lhncbc.github.io/r-snippets-bmi/regCOVID/regCOVID_data_file_descript.html and regCovid_example.R with example run.
However, I failed to find these links in the paper, which can harm the overall impression of the paper.
I would advise to aggregate response to reviewers and add them to the paper to make it more clear.


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: COMPUTERIZED MONITORING OF COVID-19 TRIALS, STUDIES AND REGISTRIES IN CLINICALTRIALS.GOV REGISTRY
Review round: 2
Reviewer: 2

Output:
Basic reporting: This is the revision to previously reviewed manuscript titled Computerized monitoring of COVID-19 trials, studies, and registries in ClinicalTrials.gov registry, submitted to PeerJ for review.
As a general comment, the overall structure of the revised manuscript addresses the questions or suggestions made to the authors. The introduction, methodology, analysis, and results are very well structured. The author's rebuttal to the major and minor suggestions have been answered well, and I do not have any further concerns from a structural or readership perspective.
Experimental design: The authors have made addition based on prior comments for CRI. This certainly helps with tying in relevance from an informatics perspective.
Validity of the findings: The results are supported by the access to raw data and R-code. The authors have made significant changes to the GitHub repository and provided extensive documentation with revised codes. The addition of weekly updates of data was found to be very useful and certainly adds high value to researchers for COVID-19 studies. No other concerns.
Additional comments: Overall, the manuscript is significantly improved with accepted responses to the questions from the previous review. The manuscript is very relevant to the current research needs and the scientific society would greatly benefit from this information. The manuscript conforms to the expectations of the PeerJ guidelines.


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: GENE FLOW RELATES TO EVOLUTIONARY DIVERGENCE AMONG POPULATIONS AT THE RANGE MARGIN
Review round: 1
Reviewer: 1

Output:
Basic reporting: Reporting is good in all respects - I did not check the raw data access.
Experimental design: This is original primary research, and the research question is well defined and meaningful.  The study meets high technical and ethical standards (if licences were required, they were not reported in the ms). Methods were described with sufficient detail.
Validity of the findings: I believe the findings are interesting and conclusions follow from the data, with some caveats that could taken up in the discussion (see next box). The data is good, and the analyses well conducted. The findings and conclusions are by and large valid.
Additional comments: I think this was basically and interesting and valid study addressing a relevant problem. My main concern with the study design is that the lab reared nymphs were field collected, and hence, it is not possible to exclude the possibility that that carry-over environmental and/or maternal effects contributed to their development in the lab. Hence, the evidence for genetic basis of the observed differences is not bullet proof, but this was not discussed in the Discussion – I think it should. In the same vein, any differences in phenology among the sites – and thereby the age of field collected nymphs – might also play in. Some discussion on this would be also in place.

Some additional suggestions

L 27. I am not sure that “a phenotypic effect of gene flow on climate-induced selection in this species” was actually shown. The study did not measure selection, and the causality of phenotypic effect of gene flow was not established – it was inferred.

L84-85. I am not sure that it is accurate to say that climatic conditions are the same. In fact, no climate data is shown, but it is assumed that climate is the same because the latitudinal range from where populations were collected is the same. In fact, the Swedish locality and the Åland locality in particular experience a maritime climatic conditions, whereas the Kaarina population is more influenced by continental climate. Climate is not only about latitude. It would have been nice to see some more characterization of the climatic conditions in the study sites (e.g. growth season length).

L265-266. This basically ok, but as we know, even speciation is possible in the face gene flow. Gene flow is not necessarily a hinder for divergence. Perhaps this could be acknowledged somewhere.

L283-285. Agreed. But one way to elucidate this would be to calculate added variance components of population differentiation – what proportion of the variance is among vs within populations. It would give heuristic idea degree of population differentiation. As the authors have access to genetic data, they could also compare the FST with PST to gauge if the degree of divergence is likely to be driven by selection. I am not saying that they should do this, but I would have done because it might strengthen the case further.

L325-327 I had difficulties understanding this sentence.

L328-329. This feels like too strong statement – there is plenty of evidence that they do, and here it is not possible to rule out the effect of environmental factors as field collected nymphs were used.

L355-366. Maternal inheritance of size in crickets reinforces my concerns above – if maternal effects are strong, then field collected nymphs are perhaps not best way to infer genetically based divergence. More cautions interpretation – or discussion of potential caveats of the approach – would be in place.


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: GENE FLOW RELATES TO EVOLUTIONARY DIVERGENCE AMONG POPULATIONS AT THE RANGE MARGIN
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript “Gene flow relates to evolutionary divergence among populations at the range margin” presents an interesting study about an aspect of dispersal ecology and evolution that is often discussed in theory or through models, but rarely addressed in real-world systems. The authors try to disentangle the effect of genetic structure and phenotypic plasticity on the phenotype of individuals in two different types of metapopulations: one sporting a low level of connectivity and one presenting regular gene flow.

Generally speaking, the manuscript is well-written, easy to follow and provides all the needed information even for a non-specialist reader to follow the narrative.
References are well-balanced, mixing classical seminal papers on the topic with more recent (< 10 years) articles on the subject.
Dataset structure is clear and linear.
The model applied has an easy structure (Appendix S1): the used priors are weakly informative to avoid constraining the MCMCs, however I would like to see a short explanation on how the priors were chosen (e.g. why those means and variances for the Normal distributions) to better follow the Authors reasoning.

The Authors declare that no specific field permit was needed to perform the experiment.

In general, I believe this paper is well-executed and suited for publication on PeerJ; I would only suggest a few, minor modifications to improve readability and address some issues I found while reading. Details are listed in the following fields
Experimental design: The project is well-structured and clearly exposed; the Introduction is detailed and provides a good overview of the state-of-the-art and the hypothesis the Authors want to test. Materials and Methods are quite well presented and adequate as well, even if I personally have some reserves about a few of the metrics that were used (see later).
Validity of the findings: Results are synthetic but nonetheless sufficient to prove the point the Authors wanted to show; in my opinion, clarity of the figures could be improved by performing minor modifications (see later).

Discussion is linear and clear, with the authors providing plausible explanations to their findings while at the same time recognizing the limits of their study without overestimating their work. I would have personally like to see a more propositive approach to some of the limits of the study: the details are addressed later on in this review.
Additional comments: Line-by-line breakdown of my comments:

-	Line 49: “Interspecific variation in body size”. It could be useful to add here what some of the causes of this variation could be, not only listing its constrains and consequences.

-	Line 64: I appreciate very much the digression about the consequences of gene flow. However, I feel that the topic is somehow incomplete: I would personally add a sentence about the “ideal” amount of gene flow and what happens when there is too little of it, in opposition to the “genetic swamping” already reported.

-	Line 150 and following: I personally do not think that simply looking at the average yearly temperature is enough to state that the environmental conditions in two sites are similar. Many other factors could be involved in shaping the local conditions (e.g. humidity, exposition to sunlight, plant communities, presence of predators…), which in turn could affect individuals body size. As this point is pivotal for the whole experiment and discussion, I would like to see it discussed more in detail.

-	Line 161: while I understand that no maternal effect has been ever spotted in the focal species, as the Authors explain later on in the paragraph, I am not convinced that collecting instars from the field and raising them in the lab would prevent any environmental effect to influence individuals growth. A more robust design would have been collecting females in the wild, let them lay eggs in the lab and then test those individuals: I would then kindly ask the Authors to provide a more robust backup for their claims.

-	Line 188: were individuals stored in ethanol immediately after reaching adulthood or a certain amount of time was given between the last molt and the conservation?

-	Line 205 and following: while I appreciate the effort the Authors put in being sure the results collected with two different methods are comparable, I can’t help but wonder why they changed sampling methods mid-way in the first place. A short sentence explaining their choice would be helpful here.

-	Line 223: I believe that in the model should also be included the effect of the site the individuals were collected from. It is possible that one site produces inherently bigger or smaller individuals for any reason: with the model as-is, this would go undetected.

-	Lines 243 and following: have the Authors performed other checks on the robustness and reliability on the model before proceeding? Standard Bayesian tests I am thinking about are the Rhat values and the Effective Sample Size of the final model.

-	Line 283-85: to the Authors’ knowledge, are there any planned genetic studies to address the issue described here? If not, I think proposing a research line here (of course without going in detail) would help making the Discussion a more propositive and not simply a list of “things we do not know”.

-	Figure 3: if the differences are calculated against the "Con" samples, those columns can be erased from the graph or placed in Supplementary if the Authors want to show the spotted confidence intervals.


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: GENE FLOW RELATES TO EVOLUTIONARY DIVERGENCE AMONG POPULATIONS AT THE RANGE MARGIN
Review round: 1
Reviewer: 3

Output:
Basic reporting: The authors showed that R. roeslii from isolated populations have longer femurs, pronota and gentialia but shorter hindwings compared to continuous populations. They conclude that this is due to restricted gene flow and climate induced selection.  Since laboratory-reared instars developed the same size as the individuals from the parental population, the authors ruled out the possibility that phenotypic plasticity based on environmental factors play a role in differences in body size.
The study is well written, interresting and overall easy to follow and understand. The provided context by the author, who shows great expertise in the background of natural history and distributional patterns of R. roeslii, was outlined very well. The figures are appropriate and easy to read and to understand. Fig 1 could profit from a northing and some additional data on genetics and population structure, which I outline in point 1 below. The authors provide the raw data inclusive the codes for analyses in a very useful manner, which I really appreciate.
Experimental design: The analyses is statistically sound. Sample size and number of populations is not huge, but sufficient for valid result with the used analyses.

I am not totally convinced that the first instars collected in the field could not have been influenced by environmental factors during embryonic development. Line 171 is not a good explanation und insufficiently cited. Since this is one of the aims of the study this could have been verified by taking adults from the field to the lab and breed them for at least another generation. This needs better references and explanation.
Validity of the findings: I generally agree with the conclusion.The different scenarios of how gene flow, genetic drift and adaptation can lead to different outcomes in isolated populations is well explained and referenced. However, the discussion on the casual mechanistic of genetics and drivers of adaptation could profit from a more straightforward explanation. Sometimes it is hard to differentiate between speculation and identification of causal drivers, which should be stated more clearly (but see point 2 below). Therefore, in my opinion, there are three general points, which I will outline in more detail, which need improvement before the manuscript would be ready for publication:
1.	The title, abstract and general conclusion suggest that this is a genetic study. I was a little disappointed not to find any genetic data in this study. Maybe a rephrasing based on the actual results and methods used in this study would avoid disappointment by other readers. The previous study from the Author (Kanuch et al 2013) supports the conclusions based on genetic data.  However it should be stated more clearly in the methods and discussion how exactly the sampled populations are structured genetically. Genetic structure and isolation could be easily depicted in Fig 1 instead of referring merely to another publication. That would save the reader a lot of work and increase readability, especially if the authors want to reach readers who are unfamiliar with the author’s former work. The study should be readable as a standalone work.
2.	In line 118 you state: “If latitudinal variation in adult morphology is the result of local evolutionary adaptation rather than phenotypic plasticity, then the size differences between isolated and continuous populations should remain in the laboratory reared individuals.” In line 306 you discuss that the increase of body size is possibly due to a colder latitude. However, in the methods in line 173 you explain:  “As eggs of all tested populations have developed in similar climatic conditions at the same latitude”. In line 353 you conclude that “characteristics of study populations are similar”.  This would contradict line 40, 118 and discussion in line 306. I am confused: is it climate induced or not? When you discuss latitudinal or temperature affects or discuss “local selection pressures” (line 301-302) you should provide data on it (e.g. latitudinal and climate differences of the sampled populations).
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: GENE FLOW RELATES TO EVOLUTIONARY DIVERGENCE AMONG POPULATIONS AT THE RANGE MARGIN
Review round: 2
Reviewer: 1

Output:
Basic reporting: In general, the manuscript is of good quality; I refer to my previous review for any aspect not specifically addressed here.

During their revision, the authors managed to address the comments provided by the three reviewers, which often overlapped. They changed/expanded the methods section when possible to incorporate the comments and, when it was not possible, explained the rationale behind their choices.
The Discussion was also improved to address any doubt the Reviewers expressed.
Experimental design: No further comment; all the highlighted issues, both about the sampling and the analysis, had been addressed.
Validity of the findings: No further comment.
Additional comments: No additional comments


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

Input:
Title: GENE FLOW RELATES TO EVOLUTIONARY DIVERGENCE AMONG POPULATIONS AT THE RANGE MARGIN
Review round: 2
Reviewer: 2

Output:
Basic reporting: According to my first review, there were no concerns about the basic reporting. My recommendations to include genetic data in Fig 1 were met in a very pleasant manner.
Experimental design: The authors addressed the concerns I raised about the field collected nymphs and possible environmental factors.  Under the described circumstances, although the method is not optimal (as explained captive reared individuals would be better, but is not possible), it is now addressed in a sufficient manner in the manuscript.
Validity of the findings: I was very pleased to see how the authors solved my comment about the inclusion of genetic results from previous studies. The new graphical illustration and the according explanations in the text improved the readability as a standalone work.

As explained in my previous review it was sometimes unclear and sounded even contradictory if the observed factors were climate induced or not. The authors rephrased the text and made their statement more clear.

I have nothing more to criticize and think the manuscript is fit for publication.
Additional comments: No additional comments


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

Input:
Title: THE ROLE OF GEOMORPHIC ZONATION IN LONG-TERM CHANGES IN CORAL-COMMUNITY STRUCTURE ON A CARIBBEAN FRINGING REEF
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Review peerj-48068

General comments
The work by Medina-Valmaseda and collaborators entitled The role of geomorphic zonation in long-term changes in coral-community structure on a Caribbean fringing reef describes a homogenization process experienced by a Caribbean coral reef. In the last 40 years (1979-2019), two “geomorphic zones”, shallow (3.7 m) front reef, and deeper (9.8 m) rock-terrace reef has become more ecologically similar. The manuscript has good quality, it is well written, and the statistical methods are appropriated. The results are nicely presented but it needs some improvement before it can be accepted for publication. My main concerns are related to the overall geological approach, rather than ecological, evidenced by the use of geological terms (and the justification for it) as well as interpretation and discussion of the results. Below, I provide suggestions/comments for authors to consider in their review process.

The use of multiple terms related to ecological and geological reef processes is unclear and to some extent confusing. Take, for example, the geo zones and eco zones indicated in Figure 1. Throughout the manuscript multiple terms [(rock-terrace (line-97), coral ground (line 54), non-accretionary communities (line 67), non-accretionary deeper hard-coral ground (line 96)] are used referring to the same reef zone (hard-ground community, HG). Something very similar happens with shallow accretionary reef front, RF. Thus, while the combination of geological and ecological aspects to analyze geomorphic zones is novel and useful, it should be accompanied by a list of terms and their clear respective definitions (I suggest this definition list is submitted as supplementary material). More importantly, the use of these terms has to be standardized throughout the manuscript.

From the beginning and throughout the Introduction section, the authors focus on reef accretion, which they defined as a process occurring over geological time scale involving framework growth (e.g., CCA and corals) and erosion (physical and biological) as well as other factors (line 34-37). The introduction of the concept, accretion, provides the background for the distinction of the two geomorphic zones “accretionary zone” and “non-accretionary zone”. If “non-accretionary zone” is similar to “coral-ground”, already defined by Rodriguez-Martinez et al. (2011) as reef communities that colonize rocky substratum but not form framework (three-dimensional structures), why not use the coral-ground throughout the manuscript? It is a simpler term, already published with which readers might be more familiar with.

The authors indicate the use of ecological snapshots to estimate the accretion potential of the reef has two questionable assumptions (line 69-70) and one may wonder how this work, a temporal comparison of coral community snapshots data, deal with those two assumptions.

Did authors establish a size limit to differentiate juvenile (e.g., smaller than 4 cm) from adult corals? Since density (number of colonies m-2) and frequency were used in their analysis, readers need to know the minimum size considered during their surveys (at the very least those conducted in 2019)

Regarding the accretion approach, what are the biological bases to differentiate between Key species (usually coined Primary frame builders) and Less influential species (traditionally called secondary frame builders)? If accretion involves physical and biological processes occurring over a long-time period that determines the balance between reef growth and erosion how then, can some species (slow-growing, branching, and massive) be classified as Key species and others (fast-growing, less structurally complex) as less influential? One could imagine that besides species growth rate, colony size, and structure, other elements might be taken into account to distinguish their role in reef accretion. A better explanation for the accretion Key species vs. accretion less influential species will greatly enhance the paper.

One of the most straightforward results from this temporal analysis is the homogenization process experience by the coral communities present in the two geomorphic zones. Yet, the discussion and conclusion mostly focus on the potential accretion (line 308, 330). I suggest the authors bring to the discussion, and maybe introduction, how they differentiate between ecological processes such as ecological succession and ecosystem resilience vs. reef accretion. For example, in line 42-44 …”Left undisturbed, this framework has the potential to accrete vertically”……a clarification of what kind of disturbances will help to understand the outcome “accrete vertically”.

Specific comments
Line 16: This first sentence of the abstract is confusing. Are the authors referring to Ecological processes or Ecological studies (approaches)?

Line 20: Define geomorphic structure

Line 39: Cite a couple of examples where CCAs are among the primary reef calcifier [examples, algal ridges of St. Croix. (Adey 1975), Atoll Rocas in Brasil (Kikuchi et al. 1997), Hawaiian fringing reefs (Littler 1973)].

Line 48-49: It’ll be more accurate to say “For example, analysis of cores drilled on Caribbean …..”

Line 51-52: Same comment as above: “…, in more hurricane-prone areas, cores obtained in the same reef zones….”

Line 53-55: This sentence is confusing and should be modified. Assuming “non-accretionary coralgal framework” is the synonym of “coral ground”, I suggest the author use the term “coral ground” since it’s been defined in the past (e.g., Rodriguez-Martinez et al. 2011) and readers might be more familiar with it.

Line 56: Eliminate “natural”

Line 67-68. In line 67 the “non-accretionary” term is defined as “communities” whereas in line 68 is considered is zone “geomorphic zones”.  As stated before, I suggest the authors choose a term (framework, community, or zone) for non-accretionary areas and stick with it. A solution could be to “coral-ground zone”.

Line 145: Replace “This is done because different geomorphic zones within a reef have a heterogeneous accretion capacity due not only to the composition of the coral community but also to external environmental gradients” with “The analysis of IVI was carried out because different geomorphic zones within a reef have a heterogeneous accretion capacity as a consequence of the composition of the coral community and external environmental gradients”

Line 182: Replace “genres” with “genera”

Line 186: Replace “genres” with “genera”

Line 190: Eliminate “the cornerstone”

Line 207. Since A. palmata, A. cervicornis, A. tenuifolia, and A. agaricites refer to two distinct genera, the genus acronym must be differentiated using, in this case, the first and second letter. Ac palmata, Ac. Cervicornis, Ag. Tenuifolia, and Ag. Agaricites.

Line 275-277: Please, add references supporting that species of Agaricia and M. cavernosa are sediment-tolerant species.

Line 306-307: Please, add the reference support this claim “….., despite the fact that geological data indicate no accretion during the Holocene”

Line 314-315: The statement “Ecological assessments assume that reef accretion is constant in time and space” can be argued over the basis what the goals of geological vs. ecological studies. I suggest the authors elaborate on it by bringing up examples illustrating their points.

Line 330: Add “,” after “consequence”

Tables and figures
Table 1. There is no need for this table since most of the information has been already included in the text [“No of transects” (line 103), ‘S” (line 182, 185), and density (line 181)]. “Average depth” can be mentioned in the Methods section and “N”, if needed, can be mention in the Results section.

Figure 3 and figure 4. I suggest, if possible at all, to use short written species name (S. siderea) instead of species acronym (SSID).

References
Adey, W. H. (1975). The algal ridges and coral reefs of St. Croix, their structure and Holocene development. Atoll Res. Bull. 187, 1–66. doi: 10.5479/si.00775630.187.1

Kikuchi, R. K. P., and Leão, Z. M. A. N. (1997). “Rocas (southwestern equatorial Atlantic, Brazil): an atol built primarily by coralline algae”in Proceedings Of The International Coral Reef Symposium, Panama, 731–736.

Littler, M. M. (1973). The population and community structure of Hawaiian fringing-reef crustose corallinaceae (Rhodophyta, Cryptonemiales). J. Exp. Mar. Biol. Ecol. 11, 103–120. doi: 10.1016/0022-0981(73)90050-6

Rodriguez-Martinez, R. E., Jordan-Garza A. G., Maldonado M. A., Blanchon P. (2011). Controls on coral-ground development along the Northern Mesoamerican Reef Tract. PLoS ONE 6(12): e28461


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 ROLE OF GEOMORPHIC ZONATION IN LONG-TERM CHANGES IN CORAL-COMMUNITY STRUCTURE ON A CARIBBEAN FRINGING REEF
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is well written and fulfills the necessary conditions of basic reporting.
Experimental design: It would be good to provide some more detail on how the 2019 transect data were handled - for example, it is not clear whether their abundance estimates are based upon colony counts or colony surface area (unless I have missed it). Otherwise, I find it to be of good standard.
Validity of the findings: This is where I have my main concern - The authors combine data collected using fairly different benthic protocols but provide no clear justification as to why this is appropriate. It is thus not clear to which extent their results might be confounded by method biases. Please see my comments for the authors for more detail.
Additional comments: Overall, I found this to be a well-written manuscript in an important topic. There is great need to rigorously assess the extent to which coral reefs have changed over time. The authors focus on a fringing reef at Punta Maroma to assess changes in coral assemblages over a 40-year period. To do so, the make use of data collected in the 1979 and 1985 as baseline and compare these data with those collected in 2019 at similar reef zones on the same reef. They use a range of multivariate statistical tools to carry out such comparisons and finally conclude that there is strong evidence of a partial homogenization of what used to be distinct Reef front and Hard ground coral communities.
The manuscript is very well written, and the authors clearly show good mastery of the statistical techniques they use. However, there is a fundamental problem underlying all their analyses, which compromises to an unknown extent the robustness of their conclusions. The 1979/1985 data used as baseline were collected using a very different sampling protocol from the data collected in 2019. In 1979/1985 data were collected using 20-m long line transects and counting the chain links overlaid of different coral species. The 2019 dataset involved using 30-m long (1-m wide) belt transects and counting and measuring the corals within those transects. Yet, in their statistical analyses the authors treat these very different sampling units as perfectly interchangeable without a clear justification of why this should be the case. They allude to a contrast-based analysis and to the fact that both data sets yielded increasingly flattening accumulation curves, but it is not clear how these points address the issue of method bias and interchangeability of statistical replicates. In my view, flattening accumulation curves do not imply absence of method-bias and it is not explicitly clear how their contrast-based analysis addresses the issue. Yet, it seems unreasonable to simply assume that sampling units of such different spatial grain sizes (line transect: 20 m x 0.01 m = 0.2m2 vs belt transect: 30 m x 1m = 30m2) applied on the same reef zone would necessarily exhibit similar statistical properties (e.g. variance and bias). As Fieberg et al (2020) recently point out (https://peerj.com/articles/9089/), the resampling methods that underlie the multivariate analyses performed by the authors assume that the sampling distribution of a statistic (e.g. Pseudo-F) “tells us about the values we might expect for the statistic if we were to repeatedly collect data sets of the same size from the same population and using the same sampling protocols”. The latter condition is clearly not met in the authors’ study. For all we know, some of the multivariate dispersion differences identified by the authors between periods (lines 244-245) could simply reflect reef zone-specific differences between methods in sample variance.
I have recently become increasingly aware of the issue of method-bias in coral reef surveys and my view is that this remains a pervasive problem in the literature, despite a considerable number of studies highlighting that it should not be ignored (for examples addressing the issue of method-bias, see https://peerj.com/articles/8167/ and references therein). Yet, it is currently not being sufficiently recognized and adequately addressed in studies seeking to compare or combine datasets collected using different methods. I also feel it is solely the responsibility of the authors to show that the probability of method-bias confounding their analyses is negligible and/or can be explicitly dealt with. Ideally, the authors should have carried out a pilot study using both methods in 2019 to demonstrate negligible or manageable method-bias to help justify their data pooling. Unfortunately, this preliminary step is hardly ever considered in the literature. Alternatively, the authors could at least point to empirical and/or theoretical studies focusing on comparisons between line transects and belt transects supporting that it is adequate to pool the data. Note that this would be obviously different from pointing to prior published studies suffering from the same problem.
Having said that, I do not question the main qualitative conclusion of the authors - I am sure that, overall, the reef zones have changed in the general direction of homogenization highlighted by the authors - My concerns revolve more around the technical soundness of the analyses allowing them to reach those conclusions and around the potential for method-biases to consistently over- or under-estimate the true magnitude of change.
Thus, I think the authors should be given an opportunity to provide an adequate justification for their data pooling, which should go well beyond what is currently offered in the manuscript, and which should be made explicit in the manuscript itself. However, if the latter is not possible, my recommendation to the authors would be to simply refrain from any statistical comparison between the 1979/1985 period and the 2019 that would assume that their data are perfectly interchangeable between those periods. The manuscript could use both datasets independently to illustrate the coral communities during each period. Most of their outputs already seem to do so (Table 2, Fig 2-4) and they could perhaps be supplemented with species richness estimators and accumulation curves for each dataset. In any case, the changes reported appear so strong that I am sure that the final take-home message will remain clear and convincing without having to compromise the overall statistical soundness of the paper.