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: 2
Reviewer: 1

Output:
Basic reporting: The paper is generally well-written, but there are a few instances where sentences would benefit from some revision. I have pointed out these in the specific comments.
I felt the Intro would benefit by ending with the formulation of a clear and explicit objective.
Figures and tables are generally fine, minus some text omissions/typos. I have pointed out these in the specific comments.
Experimental design: I have one significant additional concern in relation to the handling of the data used to compare changes in "relative abundance" between 1979/1985 and 2019 -  I provide details in the comments below. Having said that, I do not think that this concern will ultimately affect the authors' main conclusions; this concern speaks more to the technical soundness of the paper.
Validity of the findings: No further comment
Additional comments: General comments
Overall, I feel this version is much improved and that it has addressed the main issue about method-biases I had raised in my previous comments. There is also greater clarity in how the data were handled and analyzed. Because of the latter, there is one potentially additional significant issue that has caught my attention, which is the use of number of colony counts in the 2019 dataset and the number of chain links in the 1979/1985 to derive estimates of relative abundance to compare between periods. My sense is that numbers of chain links inform mainly about spatial living coverage of the different coral species, irrespective of their colony numbers, so it is not quite clear that these two metrics are directly comparable. In my view, a more meaningful comparison would have involved deriving estimates of relative abundance based on actual colony counts for both periods (since these data seem available) OR based on surface area covered by each coral in 2019 (since the data on both colony counts and colony size also seem available) and number of chain links in 1979/1985 period. Having said that, the authors have supplemented their key analyses with presence/absence data, which should be fairly robust to these data handling decisions, and the general patterns seem to hold (Table 2). As such, I would endorse the manuscript for publication after minor revisions provided that the authors give appropriate consideration to my specific comments below.

Specific comments
Line 50-53 – It is not clear what does the “however” make reference to – I get the sense that the point here is that you can have coral grounds that are not geologically accretionary because they have been subject to high levels of physical erosion by hurricanes and they are thus basically made of coral fragment remains. If that is what is meant, introducing the term non-accretionary in that sentence would help as a contrast to the previous sentence.
Line 80-83 – This sentence is not clear – are the surveys the ones in the paper or those from a different study? Moreover, the objective is not very clear – I presume that it is to assess the extent to which homogenization has occurred in these two geomorphologically different zones? It would be good to mention that historical data from the 70’s will be compared to recent data for that purpose to inform about the specific temporal period of interest.
Line 133 –comma should come after citation brackets
Line 134 – after b), sentence should star in lower case
Line 142 – Please clarify that the IVI for the pre-1990’s data is only based on the 1985 dataset.
Line 153-154 – I think the key idea here is that if the method-biases are small relative to the real signal of change, then the latter would still be reliably and meaningfully detected. The Nadon and Jokiel references could then be used to argue that previous studies comparing the two methods indicate that such method biases appear indeed to be small  - the later conceptual framework (i.e. method biases being small relative to the true signal) is probably better because using the term “virtually indistinguishable” might require clarification about whether or not their tests had sufficient power, which is often not the case.
Line 163-167 - Good.  I also agree that diversity metrics are likely to be less affected by method-biases than % coverage ones.
Line 172 – replace “…which has difficulties dealing with this using …” with “…which makes it difficult to deal with using …”
Line 175 – 185 - I feel that the method-bias issue has been sufficiently addressed in the “Method biases and uncertainties section” and I do not think that any further action is needed. In the previous section the authors provide sufficient arguments  to conclude that, although method-biases are likely, the main choice of metrics by the authors (i.e. diversity metrics), along with findings from other studies cited comparing the two specific methods at hand, suggest that these method-biases are likely to be small relative to the effects that the authors are investigating in this particular study. It is not perfect, but it is probably enough to help justify their statistical approach and it is much better than not saying anything about potential method-biases (as it was in the previous MS version).
The problem I see now in this section (lines 175-185) is that it provides a sense that method-biases can be somehow dealt with once the data have been collected. This is not true unless it is via the use of calibration/conversion curves linking both methods, which the authors do not have. I would thus recommend removing lines 175-179 and any subsequent reference to method-biases in this section. The various standardizations of the data can probably remain as they are.
Line 180-182 – Why are colony counts used to estimate relative abundance in the 2019 dataset considering that chain links are used to do the same in the 1979/1985 dataset? Using colony counts does not seem to consider that different coral species differ markedly in size. You can have a small-sized coral species (A. agaricites, P. astreoides) scoring very high in relative abundance even though overall it covers much less living space than a few but bigger coral species (Orbicella spp). This clarification is important because using the chain links to estimate relative abundance in the 1979/1985 datasets will better reflect the spatial living coverage of the different species than the actual number of colonies (unless I am missing something) [see Loya 1972 Mar Biol 13:100-122 as an example of a study using line transects to calculate both relative abundance (based on no of colony counts under a chain) and living coverage (based on no of chain links under the chain) of a coral community]. It would have made more sense to transform the 2019 dataset in relative spatial living coverage data (rather than relative abundance data), since the colonies were counted and sized, prior to calculating their relative abundance to compare with the 1979/1985 dataset. Alternatively, the colony counts of the 1979/1985 data could be used (instead of the chain links) to calculate the relative abundance of each species to compare with the 2019 dataset (as in Loya 1972). As it stands now, it might seem like comparing apples (2019: colony count estimates) with oranges (1979/1985: living coverage index), which if true could contribute to artificially create differences between time periods. I suspect I might not be the only one wondering about this and so this data handling decision will require further clarification. Perhaps one draconian (but more robust) way to deal with this potential problem would be to focus on presence/absence data only throughout the manuscript - this approach is already done in the “Diversity” column of Table 2; presence/absence data could also be used for Figures 4 and 5.
Line 220 – consider removing the commas
Line 243- consider removing the commas
Line 255 – Replace “Montastrea annularis complex” with “Orbicella…”
Fig 2 – clarify in figure header that data from 1979 and 1985 were pooled together in panels C and D.
Line 270 – insert “the” before “two zones”
Line 273 -274 – Please clarify - is it correct to use the value of the Pseudo-F ratio as a measure of effect strength when comparing among PERMANOVA factors? Does Pseudo-F ratio value not depend on the degrees of freedom (and/or levels) associated with each factor, which is likely to differ across factors?
Figure 4 – Is it possible to show the same species rows across all four panels to facilitate cross-panel comparisons in all directions? Please see my previous comments (on lines 180-182) about what these abundance estimates actually likely reflect for each method/time period. Also, it should be “…fourth root…” in header text.
Table 2 – Please clarify that normal (not in bold) font in under the two-way PERMANOVA header corresponds to the contrasts – I presume that the lines under the Factor Year x Zone also correspond to contrasts, but these (unlike the ones above under Factor Year) were never mentioned in the Methods (but I might have missed it) and it is not quite clear what they represent – moreover, one line has “RF,CG 1979” and the line below “RF/CG (79/85)” –not clear how the use of “,” versus “/” is to be interpreted.  Also, something seems wrong with the last two lines under the PERMANOVA (pair-wise tests) header (repetition of terms). Finally, the 2nd and 3rd sentence of the Table 2 header would benefit from some re-phrasing.
In relation to the PermDisp tests, is it necessary to do all pair-wise comparisons? Why not simply focus on the within-zone temporal comparisons (the 3rd and 4th lines under the header)? It would facilitate digesting these results. Also, how does the fact that the variance in CG differs between pre-1990’s and 2019 affect interpretation of the PERMANOVA results for CG, which presumably still assume similar dispersion between time periods when comparing centroids?
Fig 5 – Note that the permdisp value in the figure does not correspond with the one in the table. Replace “Montastrea annularis complex” with “Orbicella annularis…”
Line 294-306 – I think it is important to acknowledge that (1) both zones have changed markedly over time, and (2) that they done so in a manner that has led to some homogenization. I think this is the best interpretation of Fig 5 (i.e. it not only about homogenization, which could imply only one zone changing).
Line 300 – I do not recall any reference to these values (21.9% and 52.5%) in the Results section or supplementary material, but I might have missed it.
Line 313 – it might be important to distinguish between functional, taxonomic and ecological homogenization even from the Introduction and clarify which of these the MS is dealing with.
Line 318-319 – This idea is good and further developed in Line 326-335 – it might be better to integrate these two into a single paragraph at once – the Lines 320-250 dealing with the robustness of the results, which is an important consideration, could then come at the end or in a different paragraph.
Line 320 – I agree that any analysis based on the presence-absence data will be more reliable. As a suggestion, consider doing a similar figure to Fig 5, but based on presence/absence data to include as supplementary material.
Line 344 – consider adding the word “partial” in front of convergence.
Line 349 – this line would benefit from further development or details on the “regional species succession reported by Aronson and Precht (2001)”; enough so that the reader does not need to go to the cited paper to get a clearer sense of what it is implied.
Line 371-372 - Please clarify - Not clear if the contrast with Valles et al refers to identifying ecological patterns within reef types (rather than among reef types) or by using geomorphic zones or metrics other than coral coverage or a combination of any of these.
Line 376 – missing bracket.
Line 397-399- I was not sure about the basis for this statement about recruitment failure –it would benefit from further development or clarification in the Discussion or in the Conclusion itself.


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: CONSTITUTION OF A COMPREHENSIVE PHYTOCHEMICAL PROFILE AND NETWORK PHARMACOLOGY BASED INVESTIGATION TO DECIPHER MOLECULAR MECHANISMS OF TEUCRIUM POLIUM L. IN THE TREATMENT OF TYPE 2 DIABETES MELLITUS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The MS is well organized, but lack innovation.
Experimental design: The experimental design and method used in this MS is out of date. As many informations from databases were not reliably, so that some of the obtained results will mistake. In a word, integrate databases in quite not enough.
Validity of the findings: As I said previous, I can't judge the fingdings is true or not even without any experimental validation.
Additional comments: An increasing phenomenon is appeared that many researchers would like to choose network pharmacology to study herbal medicies. Howerer, if there is any improvement or innovation and just follow the routine which used previous. I don't think it is a good way to promote the development of herbal drugs. At least, experimental validation is necessary.


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: CONSTITUTION OF A COMPREHENSIVE PHYTOCHEMICAL PROFILE AND NETWORK PHARMACOLOGY BASED INVESTIGATION TO DECIPHER MOLECULAR MECHANISMS OF TEUCRIUM POLIUM L. IN THE TREATMENT OF TYPE 2 DIABETES MELLITUS
Review round: 1
Reviewer: 2

Output:
Basic reporting: Diabetes is a metabolic disease, with type 2 diabetes being the most common, usually in adults. It occurs either when there is an insufficient insulin production by pancreas or when the produced insulin is not effectively utilized in the body. These disturbances result in hyperglycaemia, or raised blood sugar, which eventually leads to serious damage to many of the body’s system over time. Diabetes prevalence has dramatically risen over the years and creates concerns. Amidst this, finding new remediation or new insights to Type 2 diabetes milletus (T2DM) will be a beneficial contribution.
Authors have used bioinformatics approach to characterize the therapeutic potential of the compounds from Teucrium polium L. in the treatment of T2DM. A comprehensive phytochemical profile mined from existing literature is presented along with network-based pharmacology investigation to decipher molecular mechanisms involved.
Introduction highlights the use of the plant extracts in the treatment in various ailments. It sheds light into its bioactive compounds and the phytotherapeutic effects.
The article is well structured, and professionally written. There are some minor issues that needs to be corrected and some sentences require rephrasing for clarity. The details of which are provided along with other comments.
Overall, the article is well within the scope and it will be of interest to the readers of the journal. The article is well organized into sections and sub-sections.
Experimental design: Research question is well defined and meaningful. The authors experimental design seems appropriate for network pharmacological analysis.
Validity of the findings: Authors have mentioned, in this study they found GSK3β, GLUT4, and PDX1 to play important role in the antidiabetic effect of T. polium. But looking at the results from this study, it hard to find their role. They are not presented in any figures or table. Although authors have discussed the compounds that interact with GSK3β and GLUT4 in the discussion section, but it is not clear whether authors found it in this study by their analysis or presented them from previous literature. For PDX1 the interacting compounds are not mentioned. It will be appropriate to refer to the findings in the study, mentioning whether it is presented (table or a figure).
In conclusions, authors mention insulin resistance and PI3K-AKT signaling pathway as the center of the mechanism of action. Authors can elaborate how they finalized these pathways to be the center. Based on the network pharmacological analysis presented in this study, there are other pathways also that seem to be involved more than insulin resistance (Figure 6 and Table 3). For instance, HIF-1 signaling pathway, TNF signaling pathway, and FoxO signaling pathway.
Additional comments: Overall, the study is interesting and a useful addition to the area. However, there are certain concerns that needs be addressed to bridge the knowledge gap. A revision is recommended for improving the manuscript.

Page 2, Line 56: Authors have mentioned “Besides these key targets, with this study GSK3β, GLUT4, and PDX1 were also shown to play important role in the antidiabetic effect of T. polium”. Authors are recommended to refer in which step they identified them.
Later in discussion section (page 8 and 9), authors have mentioned the compounds that interact with GSK3β and GLUT4 but it is not clear whether authors found them in their study or mined them from previous literature. If found in this study, the corresponding figure/ table needs to be presented. Similarly, for PDX1 the information is missing, which compounds interact and how authors identified them.

Page 2, Line 60: Authors mention only 2 pathways to be the main pathways regulated by T. polium. It will appropriate to mention how they arrived at this conclusion. On the other hand, the pathway analysis (Figure 6 and Table 3) show HIF-1 signaling pathway, TNF signaling pathway, FoxO signaling pathway, and insulin signaling pathway as well.

Figure 3: The legend mentions 32 key targets but only 31 are shown in the figure. “ESR1” is missing. Check for the discrepancy. (ESR1 is present in PPI network- Figure 4)

Figure 7: The interaction of 29 compounds with 31 key targets is presented. Again, ESR1 is missing.

Other minor comments:
Page 2, Line 61-62: It will appropriate to rephrase the following sentence for clarity, “This study reveals the relationship of the compounds and targets in T. polium”. The current sentence gives an impression that targets are in T. polium whereas targets are being investigated in humans.
Page 2, Line 68: It seems there is a typing error, “…about 1,6 million deaths...”, it should be 1.6 million.
Page 2, Line 74-75: Revise the sentence for clarity to the readers, “Teucrium L. genus….”.
Page 2, Line 76-78: Revise the sentence for clarity to the readers, “In Turkish folk medicine, treatment….”.
Page 3, Line 76-86: Italicise in vivo and in vitro.
Page 3, Line 93-94: Revise the sentence for clarity to the readers, “In blood glucose concentration, ...”.
Page 3, Line 115: Acronym TCM can be described.
Page 3, Line 120: In the following sentence it will be appropriate to write “Compounds reported from T. polium were selected based on their drug-likeness properties…”.
Page 4, Line 136-138: Revise the sentences to bring more for clarity.
Page 4, Line 143: It will be appropriate to write, “ …compounds, were subjected to…”.
Page 5, Line 164: Remove extra punctuation mark after the sentence.
Page 5, Line 182: It will be appropriate to write, “The results were listed based on their p-values.”, instead of “…due to their p-values.”.
Page 6, Line 217: Authors can mention STRING 11.0 instead of String.
Page 6, Line 237: For the consistency throughout the manuscript, it will better if authors use either p-values or p values.
Page 7, Line 278: It will be appropriate to write, “..cell function which are caused by…:, since authors are referring to two defects that arise due to long-term hyperglycemia or revise the sentence accordingly to bring more clarity.
Page 8, Line 302: Italicise T. polium.
Page 8, Line 315-136: Authors mention, “Even GSK3β has not been found as a key target in our PPI network, a large …”. But authors have mentioned in the results that they found GSK3β as a target in this study. It will appropriate to correct the sentence and provide the reference to figure/ table/ supplementary data where it was found.
Page 8, Line 316-317: Italicise T. polium.
Page 9, Line 326-328: Authors mention they find interaction of the listed compounds with GLUT4 in this study. It is recommended to provide the reference to figure/ table/ supplementary data where it was found.
Page 9, Line 328 and 330: Italicise T. polium.
Page 10, Line 370: Italicise in vivo and in vitro.
Page 10, Line 369-371: Revise the following sentence for clarity, “Though there were studies...”.

References
Page 12, Line 453, 459: DOI is missing.
Page 13, Line 481: DOI is missing.
Page 13, Line 511-512: DOI can be moved to line 511.
Page 13, Line 515: DOI is missing.
Page 15, Line 557, 568: DOI is missing.
Page 15, Line 586: Proper punctuation is required.
Page 15, Line 593: DOI is missing and “-” after punctuation needs to be removed.
Page 16, Line 602: DOI is missing and reference has repeated 2020. Delete the repetition.
Page 16, Line 610: Inconsistent referencing format. Please check.
Page 16, Line 612, 619, 621, 633: DOI is missing.

Figures
Figure 1 Legend: Since the color coding of the nodes remains the same in all figures. Authors can mention in Figure 1 that the color coding scheme is consistent across figures instead of repeating the same text in Figure 3 and Figure 7.
Figure 7 Legend: The following text is redundant as in Figure 5, “Bars represent p-values…”. It can be clearly mentioned in Figure 5 that these representations are consistent in the plots instead of duplicating text.

Tables
Table 1 Legend: Authors can simply mention T. polium. In the table heading, it will be better if authors write References instead of Ref.
Table 2 Legend: It will be appropriate to write, “…29 compounds that were used in ...”.

Supplementary data
Supplemental_data_S2 and Suplemental_data_S3: The heading can be corrected to “Gene Symbol” instead of “Gene Symbole”.


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: CONSTITUTION OF A COMPREHENSIVE PHYTOCHEMICAL PROFILE AND NETWORK PHARMACOLOGY BASED INVESTIGATION TO DECIPHER MOLECULAR MECHANISMS OF TEUCRIUM POLIUM L. IN THE TREATMENT OF TYPE 2 DIABETES MELLITUS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The authors proposed an analysis to decipher molecular mechanisms of Teucrium polium L. in the treatment of type 2 diabetes mellitus. Although some vital analyses have been performed, there are some major points that need to be addressed:

English needs to be polished. The manuscript should be formatted better and some spelling and grammar should be checked carefully. For examples, some grammatical errors and typos are as follows:

- ... were put in to DAVID database ...
- Our findings suggest its use as an effective herbal drug in the treatment of T2DM and provides new insights ...
- The ‘Compound-Target’ network consist of ...
- The top 20 results due to the p-values also suggested that compounds reported from T. polium might also leads new insights for the treatment of cancer.
- ...
Experimental design: The authors should show detail on how they performed literature search i.e., which keywords or sources that they used?

The authors transformed the compounds to SMILE format using PubChem (https://pubchem.ncbi.nlm.nih.gov/) or CS Chemdraw Ultra, so in which cases/compounds they use PubChem or Chemdraw Ultra?

Why did the authors set the confidence score as high (> 0.7).

GO database or analysis has been used in previously biomedical works such as PMID: 31277574 and PMID: 31921391. Therefore, the authors should refer more works in this description to attract broader readership.

Methodology has not been described clearly and it makes hard to reproduce the results. The authors should describe it clearly.
Validity of the findings: Some figures and network analyses are redundant and necessary. For example, Fig. 1, 3, or 4 contained few information and no-sense.

Some tables are long and it is better if the authors could put them to supplementary materials.

The authors should validate the results on an unseen data.
Additional comments: No comment.


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

Input:
Title: USING FORESTEREO AND LIDAR DATA TO ASSESS FIRE AND CANOPY STRUCTURE-RELATED RISKS IN RELICT ABIES PINSAPO BOISS. FORESTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: Here are my suggestions:
1. Many punctuation errors, phrase errors, and typos in the article need to be fixed. Free grammar and spelling check tools are available on the internet, they help identify wrong spellings and grammar issues, please go over your manuscript and check again.
2. Line 82. I suggest using a stronger mood than “might” to introduce RS application in your study.
3. Line 125 and 126 cite works of Linares, et al. in 2009, but these are two different articles 2009, please change them into 2009a and 2009b to tell them apart. Another works of Linares, et al. in 2011 also need to change.
4. Line132. 2.1 study place might be better if it changes into study area or study site.
5. Line 139. “…Paeonio broteroi-Abietetum pinsapo Asensi & Rivas-Martínez, 1976 composed…” should be “…Paeonio broteroi-Abietetum pinsapo (Asensi & Rivas-Martínez, 1976) composed…”.
6. Line 156. megapixels would be clearer than “Mp”.
7. Line 151 “1.2 Fieldwork: ForeStereo inventory” should be “2.2 Fieldwork…”
8. Line 177. The full name of the PONA project is needed.
9. Line 186. Citation of Scott & Burgan (2005) is listed in the reference.
10. Please change the symbology of the lower map in Fig 1 and leave the outline of the boundary, so the image can be seen clearly.
11. Table 1. The Italic-type description of fuel model categories needs to align altogether.
12. Table 2. The LFCC4, AR4, LFCCM, and LFCC0.25 are not explained in the article for its meaning and how to measure them.
13. Fig 3. It will nicer for readers to tell which plots are for training and validation, respectively, if different symbols or colors are applied for two groups of plots.
14. Fig 4. I see the contrast between east and west wind scenarios, but the difference would be more poping-out if both cases use the same levels from low to high. For example, when mapping the rate of spread, use a classification that encompasses slow speed on the left and fast speed on the right and apply colors from blue to red. The title of “Rate of Spread” on both sides are different. Please change them.
15. The second and third paragraph (line156-165) in 2.2 seems more adhere to the introduction of ForeStereo, so I suggest moving them to line 106 before the introduction of LiDAR.
16. The last paragraph of 2.1 Study place seems more adhere to the topic of fieldwork, I suggest moving it to the top of 2.2.
17. The error matrix of fuel model classification should be present in the article or supporting material or supplement.
18. Is there any measure besides cleaning shrubs that can be taken based on the simulation?
Experimental design: What were the metrics acquired by ForeStereo and how were they calibrated with field measurement by investigators? And What were the metrics from LiDAR used in regression? These metrics and procedures are not so clearly stated in the Material and Methods section that readers can’t figure out the analysis process until they read the results. These are especially important for future readers who do not know anything about the ForeStereo and the related procedures.

It is quite straightforward that the east wind causes worse scenarios because the topography seems to dominate in the fire environment. Will this depart from your result a lot when a different fuel moisture condition is applied? If that is the case, this simplicity (line 195-196) only demonstrates the very dry condition in this area, and if this condition is frequent in the study area, the result is convincing, otherwise, the rationale of this simplicity is needed.
Validity of the findings: You mentioned in the line 118-119 that the weak relationship between age and size. Is this because of declining growth? And your finding (in Fig 5) concert with their finding?
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: USING FORESTEREO AND LIDAR DATA TO ASSESS FIRE AND CANOPY STRUCTURE-RELATED RISKS IN RELICT ABIES PINSAPO BOISS. FORESTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: See Comments for the authors
Experimental design: See Comments for the authors
Validity of the findings: See Comments for the authors
Additional comments: GENERAL COMMENTS

The manuscript entitled “Using ForeStereo and LIDAR data to assess fire and canopy structure-related risks of Abies pinsapo Boiss forests” has the goal to combine fieldwork data with LIDAR information to characterize Abies pinsapo forests in a study area of southern Spain and to assess potential fire behavior and risk in the area.
The subject of the manuscript falls within the scope of the journal. Overall, the topic investigated is relevant and of great importance for Mediterranean fire-prone areas, particularly for biodiversity protection and forest management point of views.
The study cannot be considered original, as it combines previously developed methods already published in similar studies; nonetheless, it is an interesting work for the relevance of the Abies forests of the area.
I am not a big expert on ForeStereo and LIDAR data methodologies, so my comments will mostly focus on the fire risk part, in which several points need to be carefully revised or clarified.
The Introduction section should be enriched by adding some sentences and references to previous works that analyzed similar topics. In the present version, the fire risk part is absent from the Introduction. Furthermore, there is need to better focus the Introduction on the main goals of the work (“Using ForeStereo and LIDAR data to assess fire and canopy structure-related risks of Abies pinsapo Boiss forests”), that is some redundant parts or sentences could be omitted or shortened.
The Material and Methods section has some parts that should be better addressed and/or require additional explanations from the authors. Overall, the fire risk methods are not sufficiently complete to allow replication of the work, and the calibration of the FlamMap model is not evident. In other words, it seems that the authors used a model without any preliminary calibration and validation phase. The Results and Discussion sections need to be strengthened and revised, and should be improved taking into consideration the Specific Comments below.
The length of the text is not extended (less than 350 rows), and could be reinforced to clarify methods and results, as well as to better focus the Introduction section.
The use of English could be improved to increase the text fluency and to remove some minor grammatical wobbles.
I recommend a major revision of the manuscript before publication.

SPECIFIC COMMENTS

L35: Please consider using a more generic description of the methods instead of using “ForeStereo”. Alternatively, please describe in few words the mean characteristics/goals of “ForeStereo”

L62-135: The fire risk part is absent in the Introduction section, although the authors used a propagation model to characterize fire risk in the study area. There is need for providing at least the state of the art of the application of FlamMap or other models at the Spanish, European or Mediterranean level, as well as the potential limitations/strengths. In addition, the authors should justify the selection of FlamMap rather than other fire models (e.g.: FARSITE, Wildfire Analyst, etc.). At the EU scale, some suggested works are the following ones: Botequim et al. 2019 (https://www.publish.csiro.au/wf/WF19001), Alcasena et al. 2018 (https://www.sciencedirect.com/science/article/pii/S0301479718311551), Mallinis et al. 2016 (https://www.mdpi.com/1999-4907/7/2/46), Salis et al. 2016 (https://www.publish.csiro.au/wf/WF15081).
Likewise, please mention other previous works that (at least at the Spanish level) used remote sensing/LIDAR data to characterize surface and crown fuels and then inform fire spread/risk models.

L140: “The forest is placed in a steep valley of 252.59 ha”. I would suggest using “of about 250 ha”.

L137-157: The description of the “Study place” (or better “Study Area”?) section should be improved and modified.
The second paragraph (L149-157) should be merged with another section, because it contains methodological details rather than a description of the study area. The first paragraph (L137-148) could provide some other details, as for instance the main climate (e.g.: annual rain, winds, maximum temperatures in the summer season) and the fire regime of the study area.

L192-196: Please clarify in a sentence how the fuel models classification of Scott & Burgan was adapted to Southern Spain climate conditions

L202-204: Please provide the final resolution of the landscape file

L204-205: This is something that needs a clear explanation. As the authors know, fuel moisture files are mandatory files for FlamMap simulations, and so it is not possible to run FlamMap without these files. Please provide in a Table the moisture values associated with each fuel model for your simulations.

L205-207: Please specify if spot fires were simulated or not. If the answer is yes, please consider to provide the spot probability and spotting delay values used for FlamMap runs. Plus, please specify the simulation time (unlimited per each fire ignition, or how many hours of propagation?)

L226-228: The fire simulation results are not described. The reference to Figure 4 is not enough. The next lines (L244-255) are probably more appropriate in the Results part rather than in the Discussion.

L245-248: The authors reported that “Spread rate shows an average value of 54.85 m∙ min-1 in Levant and 22.85 m∙ min-1 in Ponent winds. More than 50% of the area is affected by a flame length above 30 m in Levant winds, whereas in Ponent winds this is only the 16.1% of the area”. The spread rate values are very high, particularly because wind speed was moderate (16 km h-1). For instance, 54.85 m min-1 corresponds to about 3.3 km h-1, that is a lot. How do the authors explain these values so high? Are these spread rates common in the surrounding mountain areas? The same consideration is valid for flame length, which is on average very high. Please provide your comments on this. Furthermore, please compare your fire behavior results with those reported in similar studies carried out in the Iberic Peninsula or in similar Mediterranean-climate areas, and improve the discussion of the study in the light of this comparison.

Figures 3 and 4. Please consider using easier classification values in the legend (e.g.: 20 rather than 21.4, 40 rather than 42.9, and so on). This could help readers. In Figure 4, please use the same scales when comparing BP, SR and FL values.


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: USING FORESTEREO AND LIDAR DATA TO ASSESS FIRE AND CANOPY STRUCTURE-RELATED RISKS IN RELICT ABIES PINSAPO BOISS. FORESTS
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: For a better manuscript, please check again the punctuation, typo, and redundant words with Grammarly before publishing. Some instances are listed, including but not limited to these.
1. Line 42. "With this information','  we developed regression models..."
2. Line 49. "...with 'the' potential for high fire spread rate fire and burn probability."
3. Line 52.  circunmediterranean or circum-Mediterranean?
4. Line 77 ."...experienced an outstanding speciation...". Please delete 'an'.
5. Line 79. "Past climate changes have led to population migrations, and to shrinkage and fragmentation..."
6. Line 93. "...detection of forest infestations (Immitzer & Atzberger, 2014)  to estimate evapotranspiration..."
7.Line 97. "... 'the' point cloud..."


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: USING FORESTEREO AND LIDAR DATA TO ASSESS FIRE AND CANOPY STRUCTURE-RELATED RISKS IN RELICT ABIES PINSAPO BOISS. FORESTS
Review round: 2
Reviewer: 2

Output:
Basic reporting: The article must be use clear, unambiguous, technically correct text.
Experimental design: Methods should be described with sufficient information to be reproducible by another investigator.
Validity of the findings: Speculation is welcome, but should be identified by proving.
Additional comments: General Comments
This study may contribute to existing literature on “combine ForeStereo and LIDAR data to assess fire in endangered fir forests”. Research objectives are provided a new procedure to map fire risk and canopy structure spatial variability. The overall level of the paper is good, but there have some questions need to be clearly demonstrated the methods and purpose of the research. The study used ForeStereo and LiDAR data for characterizing the forest structure. The author should be noted that two methods might have measurement error, due to they focused different scale and had unequal variance. There is lack of the results to prove the consistency of two methods in the manuscript. I believe that the MS needs some clarifications and improvements before being considered for publication. A few additional comments are given below:

1. The author did a lot of analysis works and output results, but did not discussed tables and figures completely, e.g. Fig 3, Fig 4, Fig 5, table 2 etc. I suggest that author don’t just report data. The author should be good to have more discussion about the generalization of the research findings.

2.The figure captions is too simple. e.g. Fig 5, What is A and B?? I will recommend the author should be described figure captions more details and more information.

3.L206-209. The author has sampled 49 plots for obtaining tree metrics and for classifying the fuel models. This number of plots is enough for statistics analysis. The author didn’t mention why fixed the train model plots (yellow points) and validation plots (red ones). I will recommend splitting a dataset randomly into training and test datasets divided it into smaller sets for building up and validating a model.

4. L277-281. The author used Scott & Burgan (2005) suggestions to distinguish initial fuel moisture. The author didn’t mention what meaning of shaded spots (M8, HR7, and R4) , very low content (fully cured) and sunny spots (M3, M9 and HPM4).

5.L244, The author says the LiDAR pixel size is 0.25 m and the point cloud density is 0.5 points∙m-2 in ms. It means that 1 m2 could not rasterize to 1 pixel. Please check it.

6. L309-L315, The author showed that results of LIDAR metrics and ForeStereo data. The model fitting is not so good. The Canopy Cover (CC) had the best fitting model
with an RMSE less than 20%, but others showed great variance. The results might lead to failure analysis and inference. The limitations and the applicability of this work to other regions should also be discussed.

7. The ms is not easy to read. I will recommend revising the ms structure.

Additionally, I’ve found some minor concerns:
1.Table 1 , Table 1 and Table 3. please unify the digit after the decimal point in the manuscript.
2. Table 2, Please correct “tn” to “ton”
3. Please unify Kappa Coefficient (L46) and KIA
4. The predictive model formula in Table 4 should be use Mathematical equation format.


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: USING FORESTEREO AND LIDAR DATA TO ASSESS FIRE AND CANOPY STRUCTURE-RELATED RISKS IN RELICT ABIES PINSAPO BOISS. FORESTS
Review round: 3
Reviewer: 1

Output:
Basic reporting: The article must be written clearly in method section.
Experimental design: Research question well defined, relevant & meaningful.
Validity of the findings: All underlying data have been provided.
Additional comments: General Comments
This is a potentially very interesting article. The treated topic is actual and very important for assessing fire and canopy structure-related risks. It discussed " a forest inventory device, to assess fire risk and canopy structure spatial variability by using aerial LIDAR and hemispherical images". The Response letter line numbers are didn’t matching with revision MS. The author should notice next time. But, the revision appropriately addressed many of the comments raised by the reviewers. However, I believe that the MS needs some clarifications and improvements before being considered for publication. I haven't big issue to raise, only few moderate-major points. A few additional comments are given below:

1. L204-205. The author had splitted randomly into train and validation, but Figure 1 still shown Yellow points are fitting plots, and red ones are validation plots. Please check it.

2.L184, The 49 plots are used 8 m radius, and author says the LiDAR point cloud density is 0.5 points∙m-2 in ms. Please specify accuracy of GPS device. The author mention that some high difference could be due to low point cloud density (minimum 0.5 points/m2 guaranteed) as well as the fact that airborne LIDAR produces better accuracy for variables related to the top of the canopy (Hilker, et al., 2012). Why canopy cover has high R2. Please specify it.

3. My second suggestion is about the regression model (Table 3). There should be mention that method of model fit and scatterplots to show relationship derived predictive model on y-axis and field collected data on the X-axis. The model method is incomplete, insufficient and incorrect. A complete description should provide how to model fitted. I would like to know how LiDAR attributes are associated with field drive observations. Please add the statistical analysis.

Additionally, I’ve found some minor concerns:
1. The aspect 0° and 360° should be the same. Please check it.
2. Table 2, the PP(mm) and cloud(%) are all zero, please addressing in 2.2 Fieldwork subsection.


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: SMALL-SCALE DISTRIBUTION OF MICROBES AND BIOGEOCHEMISTRY IN THE GREAT BARRIER REEF
Review round: 1
Reviewer: 1

Output:
Basic reporting: In “Small- and large-scale distribution of microbes and biogeochemistry in the Great Barrier Reef”, Carreira and colleagues present an original study aimed at investigating the microbial ecology of reef waters at the scale of cm, which is of relevance considering that most field-based studies employ larger spatial scales. Their reporting is mostly clear and unambiguous, and the used language appropriate. I enjoyed reading the introduction and the contextual background to the study. It really shows that there is still much to be done to understand microbial variation in coastal waters, particularly in reef waters. The figures presented are relevant and of good quality. I could not find a link to the raw data. Also, the PeerJ structure including a separate conclusion section does not seem to have been followed.
Experimental design: The research questions posed by the authors are very relevant and well defined. The knowledge gap is correctly identified and justifies the need of the research. However, the experimental approach appears to be mostly preliminary and does not allow a rigorous investigation of the questions identified earlier. Whereas it is clear that the authors’ intention of studying microbial, viral and biochemical variation at the cm scale is successful, in order to study microbial variation at the larger scale a different kind of replication (including within site replication) is needed. Sites are compared at the large-scale based on a single deployment of the sampling gear per site. This totally disconsiders the actual spatial variation and heterogeneity in microbial/biochemical parameters that likely exists within site, based on habitat variation, exposure to currents and in relation to topographic features, bottom depth, etc... As such, it is not clear to me that the design actually allows the authors to compare across sites, and I would recommend they bring the focus to the small-scale variation their experimental design is intended to capture.
Methods are well described and clear and contain enough information to be replicated. However, I have some concerns with the correlative approach used to search for a linkage between biological and abiotic parameters. It is OK to use Pearson correlation coefficient and look for linear correlations (see lines 200-202 and 297-299), however an alternative approach would be to use the Spearman rank correlation coefficient to search for (non-linear) monotonic relationships. Especially because most parameters do not follow a normal distribution, it can be the case that the relationships between them are not linear. Using a non-parametric correlative approach may allow disentangling new patterns in the data.
Validity of the findings: Results are mostly inconclusive but relevant for others who may want to set up a similar experimental approach. Spatial replication was not ideal, as stated above, and the authors also recognized that their temporal replication did not allow capturing relevant patterns (for instance, diel variation). Underlying data have been provided and are sound and controlled, allowing applying statistical tests.
There is only minimal degree of speculation, and the conclusions are well stated and linked/limited to the results obtained in the study.
Additional comments: Please find some detailed comments below:

Line 25:
The authors state that “the small and large-scale spatial and temporal distribution of microbes (…) were determined”. This gives an impression that there is also a small and large-scale temporal sampling, which is not true. Please rephrase if possible.

Line 30:
Results showed “the highest average concentrations/abundances”; of what exactly?

Line 33:
Please make explicit that you are talking about abundance of bacteria and viruses in the biological measurements.

Line 34:
To which differences (which parameters) are the authors referring to in point 5?

Line 43:
Some authors could even argue that certain microbial community ecology parameters are only to be seen at the micrometer scale (see work by Roman Stocker’s lab for instance).

Line 142-145:
Is there a reason why phytoplankton densities were not determined by flowcytometry? This seems like the logical procedure since you have the instrument and the samples.

Lines 194-195:
The discussion on the application of non-parametric tests is somehow confusing. By stating “i.e., the values of each variable did significantly change over the locations” one would immediately expect to see results of a statistical test. To which values are the authors referring? Is it perhaps a matter of heterogeneity of variances here?

Lines 218-219:
Please make explicit you are talking about bacterial and viral “abundances” here and also throughout the ms.

Line 300:
Do you mean “bacteria correlated negatively with HPO4” and positively with viruses?

Lines 323-325:
This sentence reads very much like a conclusion and should therefore be removed from here.

Lines 423-432:
Both points 3) from spatial study and the temporal study do not actually read like general conclusions (they refer to a rather particular detail). I would therefore remove them from 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: SMALL-SCALE DISTRIBUTION OF MICROBES AND BIOGEOCHEMISTRY IN THE GREAT BARRIER REEF
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article was written clearly and the contour plots figures provided an effective way to communicate the various datasets. I recommended some additional references in the Specific comments.
Experimental design: The experimental design and analysis methods are clearly described. Further statistical analyses should be applied to the small scale dataset.
Validity of the findings: Further discussion of caveats to sample quantity and instrument precision as this relates to the primary research questions is warranted (more details outlines below).
Additional comments: Overall comments:
The article could be improved with some minor corrections, but overall, I have no objection to publication and offer only a short list of specific comments. My biggest concern is the evaluating the differences between true environmental heterogeneity and instrument precision for measuring the concentrations of chemicals and enumerating biological entities. When examining the contour plots, I can see evidence for variation between sites and days, but not necessarily much small-scale variation. The background studies introduced in the article (e.g., Azam and Stocker studies) are referring to scales on the micron level, in which case, 25 milliliters really is not providing much of a different picture than a half-liter sample because you are still three orders of magnitude off from micron level heterogeneity. Logistically, one cannot do much with 25 ul sample, but the authors should further discuss the reality of scale in this context as it relates to their theses. Adding some hypotheses to the introduction and / or results would also help clarify the authors rationale for conducting the study.

Specific comments:
Abstract.
Line 30, highest average concentrations of what?
Line 31, Do the authors mean, none of the parameters correlated with bacterial abundances / concentration? Because you do not seem to have composition data, which would be expected in order to examine “distribution”.
Line 34, should be “small scale”, not “cm scale”
Lines 34-35, Be more specific. What differences were found between sites/days?

Introduction.
Lines 50-51. Clarify the statement: “However virus-microbes’s relationship…”
Line 51. “Viruses are typically coupled with bacterial communities…” How do you mean? Composition-wise? We know that is not true. Abundance-wise? There is much debate in the literature right now about how virus to microbe ratios indicate viral lifecycles, microbial growth rates, etc, so more references are needed here.
Reference this article regarding a microbial study on scale. L Weber, A Apprill (2020)
Diel, daily, and spatial variation of coral reef seawater microbial communities. PloS one.

Methods.
Line 100. The authors stated that samples were collected at high tide for four consecutive days. But did the time of day for sampling each site vary substantially? Reef microbes have also been shown to follow diel rhythms that were not related to tide.
Line 105. Clarify “purpose built device”.

Results and Discussion.
Lines 188 and 216. Is there a reference for this CV measurement? Is this how the authors determined that there was “high small-scale heterogeneity” as reported in the abstract?

Line 217. “high” small scale heterogeneity is subjective. There can be “more variation” or “high heterogeneity” than other measurements, but there is nothing to indicate 76% is high. Also, where are you statistics for this section (Lines 216-256)?

Lines 288-291. Can more details be provided here? “…did not point to a common pattern” seems to warrant further discussion.

Line 335. Add Apprill reference from comment above.

Please evaluate how different levels of instrument precision between the different measurement could affect your results, particularly for the small scale study.

The work represents an interesting study, nice job, just a difficult question to answer with state of the art technologies available right now!


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: SMALL-SCALE DISTRIBUTION OF MICROBES AND BIOGEOCHEMISTRY IN THE GREAT BARRIER REEF
Review round: 2
Reviewer: 1

Output:
Basic reporting: The reporting is clear and unambiguous and there is now a link to the dataset. The structure has also been changed to include a separate conclusion and all other guidelines have been followed. I would like to point out an interesting and very recent study dealing with large-scale variation of microbial communities across the GBR and that should be cited for updated contextualization:
Frade, P.R., Glasl, B., Matthews, S.A. et al. Spatial patterns of microbial communities across surface waters of the Great Barrier Reef. Commun Biol 3, 442 (2020). https://doi.org/10.1038/s42003-020-01166-y
Experimental design: Methods are clearly described and the addition of a non-parametric correlative approach covers my previous concerns. I am also happy with the decision of the authors to tone down the focus on their large-scale comparison.
Validity of the findings: All points are correctly addressed, all underlying data have been provided and conclusions are well stated.
Additional comments: I was pleased to read the authors' reply and that all my comments were addressed and incorporated into this new version of the manuscript. I consider the manuscript will be ready for publication after the authors include a citation to a new literature reference that has just been published (see above).
Overall, this study provides a good contribution to a field in need of new sampling/experimental approaches that can help decipher the small-scale distribution of microbes in coral reef waters.


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: SMALL-SCALE DISTRIBUTION OF MICROBES AND BIOGEOCHEMISTRY IN THE GREAT BARRIER REEF
Review round: 2
Reviewer: 2

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: Thank you for addressing my comments in the revised manuscript. Best wishes, Linda


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: MORPHOLOGICAL AND MOLECULAR SYSTEMATIC REVIEW OF MARPHYSA QUATREFAGES, 1865 (ANNELIDA: EUNICIDAE) SPECIES FROM SOUTH AFRICA
Review round: 1
Reviewer: 1

Output:
Basic reporting: This study reviewed the genus Marphysa of South Africa based on morphological characters and molecular information.  I think that the manuscript is suitable for publication in an international journal. This is the first step for the conservation of local species in South Africa.

Some modifications are needed before accepting the manuscript.
1. The figures of pectinate chaetae and other chaetae are needed to replace. Authors use the pectinate chaetae for diagnostic characters, but the pectinate chaetae in the figures are hard to see the characters. The SEM photographs or line drawings are needed for them. Line drawings of parapodia are also helpful for understanding the diagnostic characteristics.
2. Indicating previous records in figure 1 helps to understand the distribution and taxonomic position of collected samples for readers.
3. Also, the key to species or comparative table of Marphysa in South Africa helps accurate identification for readers.
4. I recommend adding Maximum Likelihood tree.
5. In the remarks section of M. haemasoma, authors should add a paragraph for morphological comparison and explanation of taxonomic treatment between M. haemasoma and M. elityeni. Additionally, photographs of M. elityeni support comparing both species.
6. There are many typographical errors.

Best regards.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: no comment


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

Input:
Title: MORPHOLOGICAL AND MOLECULAR SYSTEMATIC REVIEW OF MARPHYSA QUATREFAGES, 1865 (ANNELIDA: EUNICIDAE) SPECIES FROM SOUTH AFRICA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper needs to be carefully checked by the English native speakers amongst the authors

have made changes throughout and some globals are required
Experimental design: not an experimental study
Validity of the findings: good study and nice images - just need to tighten up text and also the puncutuation of the synonymies
Additional comments: see my comments on the atteched pdf


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

Input:
Title: MORPHOLOGICAL AND MOLECULAR SYSTEMATIC REVIEW OF MARPHYSA QUATREFAGES, 1865 (ANNELIDA: EUNICIDAE) SPECIES FROM SOUTH AFRICA
Review round: 2
Reviewer: 1

Output:
Basic reporting: Thank you for sending the modified manuscript.
I added some modifications in 'References'.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: no comment


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

Input:
Title: MORPHOLOGICAL AND MOLECULAR SYSTEMATIC REVIEW OF MARPHYSA QUATREFAGES, 1865 (ANNELIDA: EUNICIDAE) SPECIES FROM SOUTH AFRICA
Review round: 2
Reviewer: 2

Output:
Basic reporting: some minor typographical edits required
Experimental design: Ok
Validity of the findings: all Ok
Additional comments: just some minor corrections required


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: IMMUNOGLOBULIN SUPERFAMILY MEMBER 10 IS A NOVEL PROGNOSTIC BIOMARKER FOR BREAST CANCER
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors report that IGSF10 is a novel prognostic biomarker in breast cancer and that their study, for the first time, revealed a clear relationship between IGSF10 and the tumorigenesis of breast cancer.
It is an interesting article with quality microphotographs, well-supported discussion and has potential.
However, I found the presentation of the data very confusing in some areas and a much-revised version of the article would be required.
Specifically, I would like to address the following issues:

Major
- The results from the IGSF10 analyses on their cohort should be presented clearly on the results and discussed thoroughly.
- The findings on their cohort and the TCGA data should be presented on a separate paragraph, on the results section.
- Tables presenting their data concerning IGSF10 mRNA and protein expression, as well as the correlations with the clinicopathological data, would be a significant add-on for the study. It could be added as a Supplemental Tables.
- The authors should present the number of tumour and adjacent normal tissues from breast cancer patients that they used in this study on the methods. The number of the cases is 159 as mentioned on the results (section 3 - Potential biological roles and signalling pathways related to IGSF10)?
-  The authors should add a Remark diagram

Minor
- Add the source of the secondary antibody and HRP used on the study.
- Figure 1, panel A, variable “Tumor”. The number of tumor cases (1102) is probably wrong!
- Figure 1, panel A, variable “Paratumor”. The authors here denote “normal tissue”. Should be corrected.
- Figure 2. Add the number of the patients included on the KM analysis
- The sentence “In Oncomine database, the mRNA expression of IGSF10 was much lower in breast cancer than normal tissues within datasets including TCGA Breast, Karnoub Breast (Karnoub et al., 2007), Zhao Breast (Zhao et al., 2004), Richardson Breast 2 (Richardson et al., 2006), and Finak Breast (Finak et al., 2008) (Table 1).”, should be transferred to the discussion and the table as Supplemental Table 1.
- The entitled on the results section “The prognostic value of IGSF10 in breast cancer”, refers not only to prognostic value of IGSF10, but and the correlation of the particular molecule with other clinicopathological variables. The title of the section should be changed accordingly.
- The Table 3 in which cohort refers? The TCGA study?  If yes should be mentioned on the legend.
- Figure 1, panel D. The data should be presented as box- plot.
- Supplemental figures 1-18 should be deleted
- The “breast_cancer_tissue”, “CELL_LINE”, “GSEA” , “survival”, “TCGA clinical_data” should be added as Supplemental tables, but it must mentioned on the text.
Experimental design: The experimental design is good. Changes to the presentation of the data should be made.
Validity of the findings: Conclusions are well stated, statistically sound and controlled.
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: IMMUNOGLOBULIN SUPERFAMILY MEMBER 10 IS A NOVEL PROGNOSTIC BIOMARKER FOR BREAST CANCER
Review round: 1
Reviewer: 2

Output:
Basic reporting: Cell Culture: The authors have used 7 different cell-lines in this study. It is advisable that the authors provide cell-line authenticity certification to ensure that it is the right cell-lines as claimed, due to a lot of cell-line misidentification in recent times. Additionally, this also increases the transparency of the project.

Line 101 – 107: How many tissue samples were collected from patients?

Line 111 – Manufacturer’s instructions

Line 151 – 230670_at (Kindly use the correct identifiers)

Supplementary Oncomine figure shows that around 11 datasets were originally considered. Why were the excluded from the final study?
Experimental design: How were the adjacent normal samples confirmed as non-cancerous? Figure 1B shows some cases where the expression difference between adjacent and tumour are not very significant. Perhaps this is due to adjacent normal not being completely “tumour-free” in all aspects?
Validity of the findings: The expression data from the 21 patients where RT-PCR was performed has not been included in any tables. Perhaps the authors can shed more light on this – what was the distribution like in these 21 samples? How many were IDC/ ILC type? What was the ER/PR/HER2 classification? Though this is a small dataset when compared to TCGA, it will be interesting to see if it matches the data.

The results presented are indeed interesting. However, it would be too early to consider IGSF-10 as a biomarker with such a limited validation cohort. The authors can also check for associated genes which have correlated expression with IGSF-10 in the specified pathways from GSEA analysis.

The results in Table 2 from TCGA cohort indicate that the expression of IGSF 10 decreases with stage-wise progression of BC. Was the same observed in the 21 tissue samples processed for RT-PCR? If not, what are the authors' thoughts on this?
Additional comments: This manuscript by Wang et al. explores the role of IGSF-10 as a potential biomarker of breast cancer. Though the concept of the paper has been explained well, the manuscript would further benefit from being proofread by a native speaker or a language editor.

The authors have provided IHC images & some analysis data has supplementary files – but relevant Figure/Table legends have not been provided. It would be easier if the authors can amend this suitably.


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: IMMUNOGLOBULIN SUPERFAMILY MEMBER 10 IS A NOVEL PROGNOSTIC BIOMARKER FOR BREAST CANCER
Review round: 1
Reviewer: 3

Output:
Basic reporting: Please have a look at Minor concerns: 1 to 2.
Experimental design: Please have a look at Major concerns: 1 to 7.
Validity of the findings: No comment.
Additional comments: Breast cancer is one of the predominant types of tumors in women worldwide. Despite great progress in the early diagnosis and treatment recently, drug resistance and distal metastasis remain major causes of cancer-related mortality. Immunoglobulin superfamily member 10 (IGSF10), as a member of the immunoglobulin superfamily, is broadly expressed in both gall bladder and ovary. In this manuscript, Dr. Mengxue Wang and colleagues looked at the role of the IGSF10 in diagnosis and prognosis of breast cancer. The study’s conclusion showed that IGSF10 was expected to be used to predict the prognostic survival of breast cancer. Although the current study is interesting, there are some major concerns that need to be addressed before consideration of publication.

Major concerns:
1. “Materials & Methods – Patients and tissue samples of breast cancer” Line 105-106. Please provide the approval number of this study in the Institutional Ethics Committees.
2. “Materials & Methods – Patients and tissue samples of breast cancer” Line 102-104. Please provide the table of the clinical and pathological information for the “Tissue samples of breast cancer” as same as “fully clinical information of TCGA”. In addition, please analyze the correlation between IHC score and the clinicopathological information of breast cancer patients. (Line 124-139, and Line 188-206)
3. “Result – 1. The expression of IGSF10 in breast cancer” Line 172-174, Figure 1. “…the mRNA expression level of IGSF10 was significantly down-regulated in breast cancer tissues compared with normal tissues.” There is a difference between tumor adjacent normal tissue and normal tissue. Be sure to use well-defined words throughout the manuscript.
4. “Result – 1. The expression of IGSF10 in breast cancer” Line 180-183, Figure 1C and D. Please provide a larger magnification of the micrograph. From the available images in figure 1C, it appears that the normal breast tissue is closer to hyperplasia.
5. “Result – 1. The expression of IGSF10 in breast cancer” Line 183-186. Please provide the protein expression level of IGSF10 in cell line.
6. “Result – 2. The prognostic value of IGSF10 in breast cancer” Line 194-195. “Patients with high expression level of IGSF10 were significantly associated with better OS (Figure 2A) and RFS (Figure 2B) than those with low levels of IGSF10.” Please explain how to define the high and low expression groups of IGFS10. In the survival curve of figure 2, the case number of each group, Hazard Ratio, 95% confidence interval of ratio and P value should be indicated.
7. “Result – 3. Potential biological roles and signaling pathways related to IGSF10” Line 208-218. Why GSE1456 was used in GSEA analysis? TCGA dataset can also be used for GSEA analysis. Therefore, I suggest the authors should add the GSEA analysis of the TCGA dataset and display the common pathway appearing in the two datasets (TCGA and GEO1456), so as to increase readers' understanding of the potential functions of IGSF10.

Minor comments:
1. All images need to be reformatted to ensure the readability and aesthetics of the comments.
2. Be sure to use well-defined words throughout the manuscript.


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

Input:
Title: IMMUNOGLOBULIN SUPERFAMILY MEMBER 10 IS A NOVEL PROGNOSTIC BIOMARKER FOR BREAST CANCER
Review round: 2
Reviewer: 1

Output:
Basic reporting: The manuscript in the current form is adequate for publication.
Experimental design: All my comments are answered.
Validity of the findings: No comment
Additional comments: In Figure 1, panel A, C, G, the word “Paratumor” should be corrected to "normal tissue". All other comments are adequately answered.


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: IMMUNOGLOBULIN SUPERFAMILY MEMBER 10 IS A NOVEL PROGNOSTIC BIOMARKER FOR BREAST CANCER
Review round: 2
Reviewer: 2

Output:
Basic reporting: Line 28: "Broadly expressed"? Do the authors mean high expression or widespread expression throughout the organ? The intended information is not clearly conveyed.

Line 62: It would be advisable to follow a uniform pattern of providing citations.

Line 64-65: Previous study/ previous studies? There are 2 citations

Line 88-89: The authors may add a note that MCF-10A is a non-tumorigenic cell-line. It would help the readers better associate with the research.

Line 93: the line may be re-phrased to specify "used/utilized" rather than collected, as there is no actual collection happening in this case. Additionally, a citation to the original Breast cancer TCGA paper would also be advisable.

Line 94: 700 samples were used in this study - were the other samples excluded for any specific reason? What were the inclusion/exclusion criteria?

Line 99-100: Was sample collection during the time of surgery, or during a biopsy? Information not provided. The number of samples collected also is not mentioned here.

Line 134: fold change of 2 or absolute fold change?

Line 145: How was GSE1456 chosen?

Line 154: Which is the right number of samples? 700 or 1095? Please clarify. There seems to be conflict between the methods and results sections.

Line 156: Figure number?

Figure 1A/B: The authors can either label it as adjacent normal or add a note in the text as para-tumor. It would be easy for the readers if uniform nomenclature is used throughout the manuscript.

Figure 1H: label to be "MDA-MB 231" - to be corrected.
Experimental design: The authors mention 21 samples (paired) for qPCR and 31 for IHC. How many samples were used for both? Was the data compared? If not, what was the reason why the same patient sample was not used, especially if collected from a surgery where there will be more tissue availability?

Line 157: How many times was the qPCR performed? Were the results consistent across repetitions? What are the values shown in Supplemental Table 1? Are they Ct values? In many cases, there seems to be no difference between the normal and tumor. There is no legend/key provided. Similar issue for S. Table 2 as well.
Validity of the findings: The findings show no or very low significance in most of the clinical parameters taken from the large TCGA dataset when compared between the high and low gene expression groups. Only in T1, there is a significance, but it may be due to a number of factors, and hard to convince as a biomarker for breast cancer.

The authors will have to validate their findings in a larger cohort, especially with an overlap of samples used in IHC and qPCR, to be more confident of the results.
Additional comments: The authors' responses to the previous review comments seemed convincing. Sufficient proof regarding the doubts on IRB approval, consent forms, and cell-line authenticity have been provided. However, the manuscript as such is still lacking some critical elements, as pointed out above. It would be in the best interest of the work, to address these issues at the earliest.

The authors mention in the rebuttal that the manuscript has been proof-read, however, there are still many factual and textual errors in the paper. The general flow in the manuscript also seems erratic. Results section 1 mentions TCGA data twice, but different numbers and causalities. Kindly look into it patiently and make sure there are no oversights.


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: IMMUNOGLOBULIN SUPERFAMILY MEMBER 10 IS A NOVEL PROGNOSTIC BIOMARKER FOR BREAST CANCER
Review round: 2
Reviewer: 3

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: Please have a look at Major concerns: 1 to 3.
Additional comments: Breast cancer is one of the predominant types of tumors in women worldwide. Despite great progress in the early diagnosis and treatment recently, drug resistance and distal metastasis remain major causes of cancer-related mortality. Immunoglobulin superfamily member 10 (IGSF10), as a member of the immunoglobulin superfamily, is broadly expressed in both gall bladder and ovary. In this manuscript, Dr. Mengxue Wang and colleagues looked at the role of the IGSF10 in diagnosis and prognosis of breast cancer. The study’s conclusion showed that IGSF10 was expected to be used to predict the prognostic survival of breast cancer. Before further consideration of its publication, the authors must carefully revise the full text as required and provide corresponding research data as support.

Major concerns:
1. “Response to Major Q4” As can be seen from the pathological picture in Figure 1C to F, there is no typical breast cancer tissue in the micrograph!
2. “Response to Major Q5” As far as I know, the epidemic in mainland China has been well controlled in May, and I haven't heard of any laboratory that has been closed up to now.
3. “Materials & Methods - IHC” Line 120-125. “The IHC staining intensity scoring criteria were as follows: 0, none; 1, weak; 2, medium; 3, strong. The scoring criteria for the proportion of positive tumor cells were as follows: 0, < 5%; 1, 5%–25%; 2, 26%–50%; 3, 51%–75%; 4, > 75%.” The authors should explain how the immunohistochemistry score in the adjacent control tissue was calculated.


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: IMMUNOGLOBULIN SUPERFAMILY MEMBER 10 IS A NOVEL PROGNOSTIC BIOMARKER FOR BREAST CANCER
Review round: 3
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: Breast cancer is one of the predominant types of tumors in women worldwide. Despite great progress in the early diagnosis and treatment recently, drug resistance and distal metastasis remain major causes of cancer-related mortality. Immunoglobulin superfamily member 10 (IGSF10), as a member of the immunoglobulin superfamily, is broadly expressed in both gall bladder and ovary. In this manuscript, Dr. Mengxue Wang and colleagues looked at the role of the IGSF10 in diagnosis and prognosis of breast cancer. The study’s conclusion showed that IGSF10 was expected to be used to predict the prognostic survival of breast cancer. The paper is improved and most concerned raised by the reviewer have been addressed. I think it is might suitable for publication at this version of revised manuscript.


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

Input:
Title: GENOMICS VERSUS MTDNA FOR RESOLVING STOCK STRUCTURE IN THE SILKY SHARK (CARCHARHINUS FALCIFORMIS)
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript fully meets PeerJ standards. The english is professional and unambiguous, the figures are well prepared and informative. Raw and supplementary data are included and the previos MER review and the improved version (with track changes) were a nice add.
Experimental design: The research is within the Aims and Scope of the journal. The questions is well defined and relevant. The methods are described in detail and all info is included such as the raw data and the supplementarymaterial.
Validity of the findings: Please check the "General comments for the authors" field.
Additional comments: First of all, congrats for the authors for the manuscript. It is clearly written in professional, unambiguous language. The Figures are informative and well described. I’ve included my considerations/suggestions within the attached PDF file.

In general, this is a really nice and already revised, and improved manuscript. It definitely deserves to be published since it touches a sensible point regarding the recent high-throughput molecular methods, i.e., its cost effectiveness. However, the choice for the pool-seq is not only related with the per sample cost but to several parameters and I suggest to stress this out along the Discussion and also within the manuscript’s Conclusions. However, I finished the manuscript without a clear idea on how much cost a unique sample in both compared techniques and I believe, regarding the scope of the manuscript, that it should be a nice and important result. Ok, it will vary a lot depending the chemistry, platform, laboratory, etc, etc… but I believe we should finish reading this manuscript able to figure out the magnitude of costs per sample we are talking about.

Together with the points presented within the PDF, please check the Competing Interest Statement since there is no CIS, just a sentence saying that one of the authors is a PeerJ Editor. A formal CI Statement should be included prior the acceptance following the PeerJ guidelines for submission. The raw data as well as additional supplementary material are available and are a great source of info. Thanks for providing them.

Finally, I commend the authors for their work and manuscript. Imho this manuscript is good to go.


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: GENOMICS VERSUS MTDNA FOR RESOLVING STOCK STRUCTURE IN THE SILKY SHARK (CARCHARHINUS FALCIFORMIS)
Review round: 1
Reviewer: 2

Output:
Basic reporting: Kraft et al. present a manuscript entitled “Genomics versus mtDNA for resolving stock structure in the silky shark (Carcharhinus falciformis)”, where they tested the use of pool-seq as an alternative, cost effective and more sensitive tool for the delination of the C. falciformis stock structure. They examined the population structure from four different geographical sites of the Silky Shark C. falciformis. The advantage of this study is that they used the same individuals examined by Clarke et al. 2015, who used sanger sequencing of mtCR of these populations, and therefore were able to compare their findings and limit any introduced variation. Findings showed that the pool-seq revealed similar Fst values to Clarke et al. 2015, but also revealed finer structure which was not picked up by sanger sequencing on mtCR. In my opinion, this manuscript fills an important gap in the field of conservation genetics of elasmobranch, which has been hindered and restricted by the use of few mtDNA and microsatellite markers only. The huge genome size of many elasmobranch species and lack of reference genomes in many cases has also contributed to the limited advancement in this field. I believe this work will contribute towards filling this gap. However, I do have few concerns regarding few points in the manuscript, I listed these concerns based on scale and mentioned them in two sections; major and minor comments as listed section 1.3.

1)	Structure and Criteria:

1.1: Basic Reporting:
The manuscript is written in clear English and follows a logical flow. Authors introduced the subject well and transition points were well in place with sufficient referencing to the needed background.
Experimental design: 1.2: Experimental design:
The manuscript has clearly stated the research question, the gap intended to fill which fits within the scope of PeerJ. Methods are well explained, reproducible but need to provided more information to evaluate the findings (which I mention in the major and minor comments).
Validity of the findings: 1.3: Validity of the findings:
The data are made available in repository. I was happy to see that the data were analyzed and validated using two different systems in measuring Fst, which seems to be a center of debate in pool-seq. These two methods were the poolfstat and popoolation. The conclusions are clearly stated and connected to the main question investigated.

In general, the study is well presented. However, I do think the manuscript still posses some parts that needs clarification and perhaps modifications. In the general comments for the authors section, I will present the major comments followed by another section that is more specific and minor.
Additional comments: -	Major comments:

1)	Authors have noted in their manuscript that in order to reduce cost, it is important to have a large number of samples in the pool, I think its important to also mention to the readers what challenges (e.g. sequencing errors) come with increasing pool size, how it effects the accuracy of allele frequencies and may be list some reference that mentions solutions to handle this challenge. May be add a few sentences in the discussion to highlighting this point and to handle it.

2)	Identification of rare variants: Rare variants are very useful in identifying fine-scale structure, and I think it would add more strength to your argument of using pool-seq with elasmobranchs, given that population structure in most elasmobranchs is determined at a fine scale. In your study you have chosen to set your MAF to 5% (Methods, in line-189), which has very likely removed informative rare variants and possibly some private variants that could be very useful in identifying fine scale population structure. I understand the risk here is that these rare variants could be confounded with sequencing errors specially in pools with large sample size, generating many false positives. But I have two points that I would like to suggest in here:

a.	 First; would you consider changing your MAF to 1% instead of 5%, since you pools are composed of a mean of 36 individuals (72 autosomes), you optimum lower detection limit for variant alleles in your pools will be: 1/72 (AF= ~ 0.01).
b.	Second; if you decide to change your MAF to 1%, it would be useful to verify the accuracy of MAFs in your pool-seq by using CRISP [Comprehensive Read analysis for Identification of Single Nucleotide Polymorphisms (SNPs) from Pooled sequencing] to remove spurious variants due to sequencing errors yet still incorporate real rare variant alleles (As was presented in Anand et al. 2016, which you also reference in your manuscript). In this paper, they also presented a filtering guideline using Kolmogorov-Smirnov (KS) test, to help validate rare variants from large pools. Have you considered using CRISP to generate quality score for each variant, then use that score to apply a quality based filtering using the Kolmogorov-Smirnov (KS) test.
Paper: Anand, S., Mangano, E., Barizzone, N., Bordoni, R., Sorosina, M., Clarelli, F., ... & De Bellis, G. (2016). Next generation sequencing of pooled samples: guideline for variants’ filtering. Scientific reports, 6, 33735.

3)	Estimates of genetic differentiation Fst: The manuscript main objective is to validate the use of pool-seq by comparing it with mtCR of a published study (Clarke et al. 2015), yet in the main Figures of the manuscript there is not a single Figure that clearly shows and highlight the results of this comparison. The results are distributed between Figure 2 and table S2. I think its important to combine these two into Figure 2 so the reader has an immediate access to this comparison which is the main core of the study.

-	Minor and more specific comments:

•	Abstract:
Line-38: In this line where you mention “thousands” of nuclear markers, I suggest to replace “thousands” by the exact number of nuclear markers that you have actually used after filtration.
•	Introduction:
Line-49: Many elasmobranchs through out the ocean; the reference of the ocean here is quite vague and does not add value, I suggest you either drop the ocean or be more specific, for example; Many elasmobranchs through out the five ocean basins…
Line-72: the reference Domingues et al. 2017a: I believe the “a” is left by mistake as I only see one Domingues et al. 2017 in the reference list.
Line-106: I understand that within the scope of this paper you are focused on evaluating pool-seq functionality compared to mtCR, as these were the data provided by Clarke et al. 2015 and you are using the same individuals. But as you mentioned earlier in your introduction, the combination of mtDNA and microsatellites for the assessment of population structure in migratory species is essential. Could you add a sentence here acknowledging that; in this study you are only focused on mtDNA because it was the tool tested by Clarke et al. 2015. Also, it could be useful to add a sentence mentioning that one of the additional advantages of using pool-seq is the fact that through one tool you would be able to analysis both mtCR and nuclear markers, SNPs in this case, which are also easier to score and analyze than microsatellite (e.g more prone to genotyping errors effecting the analysis through; null allele, slippage, or allele drop-out). I think this could be another reason to justify and support your call to use pool-seq as an alternative tool.
Line-123: Again, Domingues et al. 2017b, there is only one Domingues et al. 2017 in the reference list!!
Line-124: At the end of this paragraph, could you provide a sentence explaining why you think Domingues et al. 2017 showed different results than Clarke et al. 2015 between the north and south Western Atlantic. (i.e. possibly due to sampling higher number of samples and the south western Atlantic was represented by a further south samples).
•	Methods:
Line-152: the sentence “Number of individuals per samples are displayed in Fig 1”, what do you mean by “per samples”? Sample pool? Also the number of samples obtained from Clarke et al. 2015 is the same as the listed samples in the map, however you have dropped some samples that showed degradation or were overly digested from the pool-seq. Could you add a sentence to clarify the net number of the used samples per location/pool after dropping the degraded samples.
Since pool-seq is based on estimates of the allele frequencies of the pooled samples, and you do not obtain individual genotyping data that are needed to run the basic assessment of neutrality (HWE and LD), I would suggest to generate a figure showing the overall distribution of allele frequency from each pool and evaluate their distribution trends compare to each other. For your SNP outlier test, I assume it was a PCA assessment? If what you have performed is a PCA outlier test, I think having a figure in the supplementary on the distribution of allele frequency from each pool is useful and will give the reader more information to evaluate the state at each pool. I believe all your selected SNPs are bi-allelic so the expected HWE distribution for your SNP markers would be a binomial distribution, would be interesting to see how they deviate from that and if this deviation is the product of structure or genotyping error (compare the distribution between structured groups compared to overall).
•	Results:
Line-236: 30 SNPs is quite a low number, another reason why changing MAF to 1% could add more information to the analysis.
Figures and tables:
-	Figure-2: As mentioned earlier, I think it would be very useful to modify this figure to incorporate Fst values generated by Clarke et al 2015. I am aware that you have mentioned it in the manuscript text, but having it in a figure is also useful.
-	Fig.2: RD or RS?!!
Supplementary data:
- I have noticed that your supplementary tables do not have headers and figures were provided with out captions, could you kindly add this information.
•	Discussions:
- Line-286: rephrase: “Pool-seq was able to detect isolated populations within the Gulf of Mexico, in the Western Atlantic, and along the Brazilian coast, where Clarke et al. (2015) found no population structure”. Please correct me if I am wrong, my understanding is that you had one sample site from Gulf of Mexico? While in this statement you mention that you detect isolated populations “within the Gulf of Mexico” is that righ?

I think it would be important to clearly mention in few sentences at the end of your discussion that pool-seq is a cost effective tool but is limited. For high budget projects its more reliable and informative to other tools such as RADseq and SNP array which are individual based genotyping methods that will allow deeper assessment of the sampled populations. However, pool-seq is suited for cases that needs rapid and cost effective assessment to serve the immediate and extensive need in providing population structure studies to serve their management.
•	Acknowledgment:
Please provide what is supposed to be filled in place of  “#XXXX” in line 380 and 381.


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: GENOMICS VERSUS MTDNA FOR RESOLVING STOCK STRUCTURE IN THE SILKY SHARK (CARCHARHINUS FALCIFORMIS)
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: The manuscript really improved during the review proccess and as far as I'm concerned it is good to go.
Do not forget to change the "XXXXX" (Line 435) for the correct number.
Warm regards
Cesar


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: GENOMICS VERSUS MTDNA FOR RESOLVING STOCK STRUCTURE IN THE SILKY SHARK (CARCHARHINUS FALCIFORMIS)
Review round: 2
Reviewer: 2

Output:
Basic reporting: Kraft et al. present a manuscript entitled “Genomics versus mtDNA for resolving stock structure in the silky shark (Carcharhinus falciformis)”, where they tested the use of pool-seq as an alternative, cost effective and more sensitive tool for the delination of the C. falciformis stock structure.
Experimental design: The manuscript has clearly stated the research question, the gap intended to fill which fits within the scope of PeerJ. Methods are well explained and reproducible.
Validity of the findings: Conclusions are clearly stated and connected to the main question investigated.
Additional comments: Thank you for providing a clear response, your work will provide a valuable addition towards the evaluation of genetic structure in elasmobranchs. All the best!


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: STRUCTURE AND FUNCTIONS OF YELLOW-BREASTED BOUBOU (LANIARIUS ATROFLAVUS) SOLOS AND DUETS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper is in general good writing; some sentences need more explanation (see comments). The paper is focused on a particular genus and the majority of the information is bias in that direction. I will recommend that authors use examples from other species in other tropical regions that study duets and diel patterns for example. The paper provides new important information for the group of investigators that study boubous, about duets as mentioned before, the discussion is biased to this group, so this makes this manuscript poorly attractive to other duet investigators.
Experimental design: My main concern is with the method of multichannel recording. Authors need to explain more how they recognize each pair and individual. For example, they can provide actual Raven screen captures, where they signaling how they separated continuous pairs unambiguously. Additionally, they did not explain well how they solve the ambiguous ID and how that data was included in the manuscript.
Validity of the findings: In general, the manuscript is well writing and results look interesting and well analyzed and presented.
Additional comments: Line 48: add a reference
Line 50: add a reference
Line62-63: this sentence is unclear, what are you trying to summarize
Line65-66: Although the information in this sentence is true, as is presented looks like that we do not know anything about duets. This appreciation is unfair, because a lot of work has been made to understand the functions, and we know very well some functions and codes. So, I recommend changing how this is presented to avoid intruding on a mistake in the duet knowledge.
Line 129-131: How using a microphone array you can describe male and female vocalizations and the context use?
Line 133-135: It is clear for you, but not for a reader. Please explain better this sentence.
Line 135-137: Why this information about the other boubou species is important?
Line 138-141: After read your introduction the information in this sentence is unclear. You need to explain more your idea that a small distribution range will affect duet behavior. Additionally, without a phylogenetic tree or information is hard to understand if your selected species is the base of the group or is more recent in origin. I say this because it is important to understand the phylogenetic relationship to disentangle the habitat effect from species distribution.
Line 154: change sols for solos
Line 242-243: You need to explain more in detail how the information in this sentence. What are all recognitions? When occurred a doubt? What this means:  was checking, in detail, characteristics of a particular bout?
Line 243-246: You need to provide more information about this method, with detail enough for a reader that never read the Linhart et al., 2019 paper, could understand how you recognize male vocalizations in your recordings
Line 248: What is a doubt?
Line 252-255: Unclear
Line 257-258: How common this occurs, please add a number of observations, and how many times you observed this occurring?
Line 434: what is the meaning of: Calls or songs?
Line 438: what is a stable repetition rate? Add more information about what is a repetition rate
Line 440-441: Songs are very diverse in bird species. So, if you defined song as: “vocalisations used for advertising mate or territory ownership”, why to say that “male phrase types are the equivalent of song types”. This makes that a reader thinks that your song definition did not work. Delete this sentence.
Line 449-452. You mention here visual observation but in methods is little or nothing about how much visual observation was conducted to associate vocalizations with behavior.
Line 456-564: These sentences are results
Line 490-492: This sentence is unnecessary for your discussion because did not provide support or discussion to your idea of the sex role in vocalizations.
Line 502-504: Add more information about why you suggest this.
Line 509-515: Very speculative paragraph without support information. Delete it.
Line 525-527: Something that may help you to understand the diel patterns is to refer to other tropical species studies where was analyzed the diel pattern for solo and duet songs.
Line 544: You need to provide examples of species where females vocalize more than males, it is important the contrast.
Line 551: Could be that the female vocalizes more in aggressive context because this reduces the probability that her male will be stolen for another female, as has been proposed in other species?
Line 556: They are truly monogamous or have extra-pair copulations? How EPC will affect the territorial behavior between females?