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: ANCIENT GENETIC DIVERGENCE IN BUMBLEBEE CATFISH OF THE GENUS PSEUDOPIMELODUS (PSEUDOPIMELODIDAE: SILURIFORMES) FROM NORTHWESTERN SOUTH AMERICA
Review round: 1
Reviewer: 2

Output:
Basic reporting: The present study tests the hypothesis that the species nominally recognized as Pseudopimelodus bufonius and P. schultzi from Colombia correspond to more than two different evolutionary lineages using two molecular markers (COI – mitochondrial - and RAG2 - nuclear). Although this hypothesis is very common in DNA barcoding studies, the authors did not mention the methodology, what it was not expected for me. But, I think it was interesting use tools from phylogeography field to identify the different lineages and what historical processes were responsible for their diversification.

Overall, the manuscript is well-writing and the language is appropriated (I listed some mistakes in the General comments section). About the literature, I think the authors used classical papers to build the introduction and discuss the results. However, 77.1% of the references have more than five years. There are a lot of new studies using fish as biological model to test the vicariance processes from Northwest of South America. Beyond that, in Brazil, there are studies using morphological and molecular data that identified and describe new species every year. So, I think you could explore more recent papers. To help you, I listed some papers that you can you in the discussion section.

All figures and tables presented in this manuscript are adequate. However, all, except by the Figure 1, need to be reviewed. Several mistakes need to be corrected and the Table 1 have to be improved. I listed these issues in the General comments section. The raw data is in accordance with the Data Sharing policy of PeerJ. However, I strongly recommend to the authors made available all sequences in the GenBank database, not only the haplotypes.
Experimental design: The authors well-designed the experiment to test their hypothesis. The samples are well distributed in different localities considered key to identify the main vicariance processes responsible for the lineages diversification: the sites are localized between important mountains and arch. The authors have the licenses necessary to collect the samples. I am just wondering if they have vouchers. If yes, please, it is necessary to provide the museum numbers.

The methods were described with sufficient detail; however, I have few questions and suggestions to improve this section. Please, see General comments.
Validity of the findings: I think the authors would explore more their findings. For example, for me, the main finding is both species P. bufonius and P. schultzi are not monophyletic. The COI is a molecular marker appropriated to delimit species and this result reveals possible taxonomic issues. I suggest the authors to bring more information about the taxonomic status of the species and write specifically about this great result that could impact the conservation of both species.

The data is robust, but I think the author should provide more information: all sequences have to be the own GenBank numbers and all samples need to be georeferenced. The information detailed are essential for other authors replicate the study.

About the discussion of the results, I think the authors misinterpreted the topology pattern obtained by both molecular markers independently. I suggest the authors to build a tree with both markers (species tree) and re-analyze the data. I listed carefully all this issue in the general comments section.
Additional comments: Major concerns

- Line 122: In the rag2 alignment I saw few problems that need to be solved: (i) in the same site (119, 282, 293, and 306) there is a gap in all sequences, so it is necessary to remove it. (ii) in the sites 479 and 480 there is a problem in the alignment. Please, fix it. (iii) Is it expected the presence of gaps (deleted sites) inside the sequence? I think it is not. The rag2 plays an important role in the rearrangement and recombination of genes of immunoglobulin and T cell receptor molecules, any changes in the open reading frame could be results in serious problems for the cell. Please, check again these gaps (see Results section). (iv) What did you do with the missing data?

- About the previous issue, I do not agree with your statement in the line 173. Because I saw gaps in your rag2 alignment (P. schultzi (H2) site 493, P. bufonius (H21) site 479 and P. schultzi (H18) site 592), I used MEGA v5.2 (Tamura et al., 2011), and when I translated the sequences, used the standard genetic code, I verified at least six stop codons. Did you check this information using MEGA?
Tamura, K., Peterson, D., Peterson, N., Stecher, G., Nei, M., & Kumar, S. (2011). MEGA5: molecular evolutionary genetics analysis using maximum likelihood, evolutionary distance,
and maximum parsimony methods. Molecular Biology and Evolution, 28, 2731–2739.

- Line 145: Why did not the authors use a species tree with both molecular markers? I strongly recommend estimating the divergence time using a tree with both molecular markers. The species tree estimated in BEAST does not require the same individuals to be sampled for each gene nor to match individuals from one to next (Drummond & Bockaert, 2015). Because species tree method requires a priori assignment of individuals to species, the authors can consider as putative species the mitochondrial lineages defined by COI.
Drummond, A. J., & Bouckaert, R. R. (2015). Bayesian evolutionary analysis with BEAST. Cambridge University Press.

-  The hypothesis tested by the authors is very interesting and they well-designed the experiment to test it. They expected to find more than two different evolutionary lineages for the two nominal species recognized. They corroborated the hypothesis, but, for my surprise the recognized species was not monophyletic and, unfortunately, the authors did not mention about it. I strongly recommend bringing more information about the species (there are taxonomic problems between them?) and a paragraph discussing this finding.

- Line 247: How did you estimated the divergence between the nominal P. bufonius from Orinoco and Amazon river? They are not in the same clade. You can only tell us that the ancestor of the P. bufonius from the Amazon river (lineage 2) separated from the clade composed by lineages 3, 4 and 5 at approximately 11 Mya.

- Line 254: Neither in the rag2 or coi trees it is not possible to see the splitting between cis- and trans-Andean Pseudopimelodus lineages. If all the divergence events were based on vicariance (as the authors discussed), the topology pattern to affirm about this splitting is to find two main clades: one composed of lineages/species from trans-Andean rivers and other composed of lineages/species from cis-Andean basin (Sivasundar et al., 2001, Albert et al., 2006, Ramirez et al., 2017, Ríos et al., 2017, Machado et al., 2018). Clearly, this does not happen in your results.

Albert, J. S., Lovejoy, N. R., & Crampton, W. G. (2006). Miocene tectonism and the separation of cis-and trans-Andean river basins: Evidence from Neotropical fishes. Journal of South American Earth Sciences, 21(1-2), 14-27.
Machado, C. B., Galetti Jr, P. M., & Carnaval, A. C. (2018). Bayesian analyses detect a history of both vicariance and geodispersal in Neotropical freshwater fishes. Journal of Biogeography.
Ramirez, J. L., Birindelli, J. L., & Galetti, P. M. (2017). A new genus of Anostomidae (Ostariophysi: Characiformes): Diversity, phylogeny and biogeography based on cytogenetic, molecular and morphological
data. Molecular Phylogenetics and Evolution, 107, 308–323.
Ríos, N., Bouza, C., Gutiérrez, V., & García, G. (2017). Species complex delimitation and patterns of population structure at different geographic scales in Neotropical silver catfish (Rhamdia: Heptapteridae). Environmental Biology of Fishes, 100(9), 1047-1067.
Sivasundar, A., Bermingham, E., & Ortí, G. (2001). Population structure and biogeography of migratory freshwater fishes (Prochilodus: Characiformes) in major South American rivers. Molecular Ecology, 10(2), 407-417.

Minor concerns
Keywords: I did not see in the PeerJ’ author guidelines a role for keywords. I suggest one more keyword: “Colombia”. Please, order alphabetically all words.

Introduction
- Line 36: This in-text citation is wrong (Author and year). According to your reference list the correct citation is “Eschmeyer & Fong, 2017”.
- Line 38: Please, organize the genera in alphabetic order.
- Line 41: Does the distribution of both species remain controversial or just for Pseudopimelodus bufonius? In lines 45 to 47 you cited the controversial just for one species.
- Line 44: As you did with Pseudopimelodus bufonius, please provide taxonomic authority for Pseudopimelodus schultzi.
- Line 46: Does Atrato and Sinú rivers from the Caribbean basin? If yes, it is necessary to say this information because in the DoNascimiento et al.’s paper the P. bufonius is restricted to Amazon, Orinoco and Caribbean basins.
- Line 58: - Line 152: In the text-citation with two author the names are separated by “&”, not “and”.
- Line 61 The reference “Lundberg et al., 1998” is wrong. According to your reference list, there is one author in this study. The problem also happens in the line 250.
- Line 66: It is not necessary italicize the abbreviation of gene’ name.
- Line 68: The sentence started in the past “we used”, so in this line, should be “we analyzed”, not “we analyze”.
- Line 68: The right name of cox1 gene is “Cytochrome C oxidase I”. The same issue also happens in the line 112. Please, fix it.

Material and Methods
- Line 85: If the authors used muscle issues I suppose they sacrificed the animals. If I am right, where is the voucher numbers?
- Line 110: I checked the Hardman’s paper to understand the reasons about you choose the primers that amplified a short region of rag2 gene and I did not find the primers rag2-MHF1/rag2-MHR1, but just the primers IcRAG2-F1/IcRAG2-R1. Where did you get those primers?
- Lines 114-117: Is the PCR’s condition correct? The authors performed the PCR in a total volume of 30 µl; however, they use 40.6µl only of sterile nuclease free water. The total volume is much high than 30µl. Can you check the information, please?
- Lines 117-119: After the 32 cycles, do you have a final extension in the thermal profile for rag2? If so, you must inform us.
- Which purification protocol did you use?
- Lines 122 and 143: Please, use the appropriate reference for the software Geneious R10 and PopArt. See links below:
https://support.geneious.com/hc/en-us/articles/227534768-How-do-I-cite-Geneious-in-a-paper-
http://popart.otago.ac.nz/howtocite.shtml
- Line 130: According to DNAsp v5. tutorial, the haplotype diversity measure is represented by “Hd” and not “h”. Please, use the correct form to abbreviate this measure.
- Line 131: Please, insert a dot and comma after “et al.”. The correct form to represent the in-text citation is “Roza et al., 2017”.
- Line 132: It is important to say if the phylogenetic analysis conducted using MrBayes was conducted for each gene or concatenated dataset. When I saw your results, I identified trees for each gene. So, I think is necessary to say this information. My suggestion is: “Phylogenetic analysis for each gene using Bayesian inference was conducted using MrBayes…”.
- Line 152: In the text-citation with two author the names are separated by “&”, not “and”.
- Line 154: According to the BEAST manual (http://phyloworks.org/workshops/DivTime_BEAST2_tutorial_FBD.pdf), the normal distribution is not always appropriate for calibrating a node using fossil information. Can you explain I did you use this distribution to calibrate this node?

Results
Line 172: I am curious: why did you obtain short sequences for these molecular markers? Oliveira et al. (2011) after the alignment obtained 1034 bp for rag2. Ward et al. (2005) using COI universal primers get 655 pb. Did you try to use these primers?
Oliveira, C., Avelino, G. S., Abe, K. T., Mariguela, T. C., Benine, R. C., Ortí, G., ... & e Castro, R. M. C. (2011). Phylogenetic relationships within the speciose family Characidae (Teleostei: Ostariophysi: Characiformes) based on multilocus analysis and extensive ingroup sampling. BMC Evolutionary Biology, 11(1), 275.
Ward, R. D., Zemlak, T. S., Innes, B. H., Last, P. R., & Hebert, P. D. (2005). DNA barcoding Australia's fish species. Philosophical Transactions of the Royal Society of London B: Biological Sciences, 360(1462), 1847-1857.
- Line 183: I am not familiar with de designation “G4” in the substitution models. Can you explain what is it mean?
- Line 185: The posterior probability support for Pseudopimelodus clade recovered by the rag2 was 0.97, not 0.96.
- Lines 205-210: This section was a little confuse for me. In the line 206, do you talk in about the cluster obtained by rag2? If yes, please use cluster than lineage. In the line 207, lineage 2 correspond to the cluster 2? If no, please remove the divergence time of rag2.
- Once, I strongly recommend using the species tree result for this section. It is informative to build a tree with both genes than show each one. I also suggestion to show the 95% HPD values than the absolute ages. For example: 7.9 Mya (95% HPD 4.05 – 11.45 Mya).

Discussion and Conclusions
- Line 256: The reference “Hoorn, 1995” is wrong. There is more than one author in this study. The same issue also happens in the line 250.
- Line 261: Please, insert a dot and comma after et al. The correct form to represent the in-text citation is “Albert et al., 2017”.
- Line 261: Should be “Duque-Caro”, not “Duque-caro”.
- Line 270:  And about the species present in the trans-Andean rivers, do you think that correspond to P. bufonius sensu stricto?
- Line 280: I suggest: “at least five different evolutionary lineages revealed by the mtDNA analysis. The interesting result is that neither one corresponds to the two recognized species. All mtDNA lineages exhibit phylogenetic histories concordant with geological history of the Northwestern South America”. The latter sentence is not true. The authors need to check the comments above in the discussion section.
- Line 285: Please, remove “cis and”.
Reference
The reference section and the in-text citations need to be reviewed. Please, use a reference management and follow the PeerJ’s author guidelines.
- In text-citation:
Please, look at the role to use “et al.” (not “et al”, as you did in several times, for example line 72).
Line 36: In-text citations, please, insert a comma after the author’s name.
According to the PeerJ’s author guidelines “Multiple references to the same item should be separated with a semicolon (;) and ordered chronologically”. This latter is an issue in the entire manuscript. Please, correct it.
- Reference list
(i) All references (100%) in this section are not following the author guidelines. Please, correct them.
(ii) There are seven missing references, as following: “Lundberg & Dahdul, 2008”, “Sullivan et al. 2013”, “Hardman, 2006”, “Bandelt et al., 1999”, “Van der Hammen, 1960”, “Albert & Reis, 2011” and “Carvalho et al., 2011”. Please, provide or remove them.
(iii) Do not underline the doi numbers;
(iv) The full title of the Journal need to be italicized. Please, also pay attention in the Journal’ names. I identified names misspelling (line 294, for example).
(v) According to the International Code of Zoological Nomenclature, the genus must be italicized (line 330, for example).

Table and figures
Table 1
- Please, standardize the in-text citation references in the legend. Each reference, include the personal communication, shows incongruence with the author guidelines.
- In the column “GenBank accession number”, the world accession is misspelling.
- The GenBank numbers were obtained for each haplotype. I strongly recommend to the authors deposited all sequences, not haplotypes, in the GenBank. The dataset must be open.
- All samples must be georeferenced. The columns “Country” and “Origin” are not sufficiently. Please, provide the GPS for all samples.

Figure 2
Because the table and figures need to be self-explanatory, I think it is interesting to describe each cluster of Pseudopimelodus as you did in the result section. You can do this in the legend or in a footnote. The same suggestion can be applied for the figures 3, 4 and 5.

Figure 4
- The authors forgotten to mention the blue circle (Magdalena river – middle section).

Figures 5 and 6
I suggest plotting black circles (for example) in the nodes calibrated with fossil.

In the figures 2 to 6, I suggest to the author check again the haplotype numbers. For example, in the figure 3, the lineage 2 (part of nominal species P. bufonius) is composed of the haplotypes 28, 29, 32, 33 and 3. But, according to the table 1, the haplotype 3 is the species P. schultzi. Other issue happens with the figure 3 and 4: the lineages 2 and 3 does not show the same haplotypes.


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: ANCIENT GENETIC DIVERGENCE IN BUMBLEBEE CATFISH OF THE GENUS PSEUDOPIMELODUS (PSEUDOPIMELODIDAE: SILURIFORMES) FROM NORTHWESTERN SOUTH AMERICA
Review round: 2
Reviewer: 1

Output:
Basic reporting: This represent the second revision of the manuscript "Ancient genetic divergence in bumblebee catfish of the genus Pseudopimelodus (Pseudopimelodidae: Siluriformes) from northwestern South America" by Rangel-Medrano et al. The authors revised the content of the manuscript and accepted almost all suggestions tha I did. The revised version is much better than the previous, because now the analyses are robust (they added species delimitation analysis and used both markers in the species tree). However, there are several issues that need be corrected, specially the main idea to construct the result section.
Experimental design: See "General comments for the authors".
Validity of the findings: See "General comments for the authors".
Additional comments: New comments:

Material and methods
I propose to change the topic order. It is interesting starts with Genetic diversity and Species delimitation (because you first need to define how will be the putative species), following by Species Tree and phylogenetic relationship and ends with Divergence time estimation topics.

Lines 118-121: To improve the logic, I suggest start with COI marker following by the rag2 marker.

Lines 123-125: The units are not following the rules of International System Units. Please, correct this issue. For example: Should be pmol, not Pmol.

Line 124: Please, spell correct the magnesium chloride formula: It is necessary subscript the number two.

Line 138: Should be “Genetic diversity”, not “Sequence diversity”.

Line 142: The letter “V” indicates the program version should be used in lowercase. This issue also happens in the lines 156, 171, 174, 176. Please, check all the manuscript and correct it.

Line 148: Why did you compare rag2 and cox1 sequences with other species? I did not understand you. Or did you meaning “combine your dataset with sequence present in GenBank database”?

Lines 149-150: It is not possible to understand the following sentence: “Samples were compared with rag2 and cox1 sequences of species in all other genera of the family Pseudopimelodidae and deposited in GenBank using sequences of Pseudoplatystoma magdaleniatum and Pimelodus yuma as outgroup”. How did you submit the sequences in GenBank using other sequences? My suggestion is, if I understood your main idea is:
“We combined our dataset with other species from Pseudopimolididae (Table 1).  Sequences from Pseudoplatystoma magdaleniatum and Pimelodus yuma were also add to the final dataset as outgroup. All sequences obtained in this study was submit to GenBank and the accession numbers are in Table 1”.

Line 188: Should be “BEAST v1.8.464”, not “Beast V1.8.464”.

Results
I am a little concern about your results. I think the way how to present them is not the best. My suggestion is a little different:
- You have a lot of figures in this section, a think it will be better if the tree markers stay in the Supplementary section.
- Show first the species delimitation results. Here it is possible to see the hidden diversity in this two nominal species.
- Use a tree with concatened markers to show the phylogenetic relationship among the five lineages (the same determined with the analysis above).
- Show the species tree and divergence time analysis (in the species tree, not and individual tree).
Line 225: Please, standardize the word “dataset”. In the line 218 you wrote “dataset” and in the line you used “data set”.

Line 230: Italicize the nuclear marker name.

Line 230: The Species delimitation analysis also showed five lineages. The authors determined the lineage in this section based on clades observed in tree (subjective analysis). I think you can base your inference in the species delimitation analysis not in the phylogenetic analysis. For this reason, it is important to change the order for this section.

Line 232: Should be “(Figs. 2 and 3, respectively).

Line 254: Insert a space to start a new section.

Lines 259-260: The authors showed the GMYC and bGMYC results, but I did not know if the likelihood of GMYC model is greater than the likelihood of null model and if the p-value is significance. It is necessary to show this information to the readers.

Discussion
Line 313: What is meaning “a.s.l.”

Line 350: Did you get the type locality for P. schultzi, Cereté – Colombia (Dahl, 1955)? If yes, the following sentence is not correct: “indicating at least five new candidate species”, because one P. schulzi lineage represents the nominal species, and the other two can be a potential new candidate species.

Figure 1: There is a color mistake. The circle represent the Magdalena River upper sector is not dark blue in the map. It is a light blue as Cauca River-upper and middle sector. It is not possible to distinguish them.

Figure 6: The Lineage 4 is not a monophyletic in the divergence time estimation. However, in the figure 4, use the same markers it is. Why did this happen?

Figure 6: There is no black circle denoted the calibrated nodes.

Figure 6:  The authors missed to insert the node supports on the tree.

Old comments (Answers for the previous review):

- Voucher numbers: I do not agree with the authors answer about this topic. It is not adequate to give the information about the voucher numbers in other paper which was not published yet. The readers need to know this information in the present study. So, I strongly recommend writing this information in the Table 1 or supplement material.

- The author given the information about GPS for all samples as suggest. However, they still use haplotype information in the Table from Supplementary material. What is the problem with that? There are haplotypes (H18, H8, H12, H1, and H19) present in more than one sub-basin and the locality information is wrong. For example: in the supplementary material the haplotype H18 is from “Magdalena River-upper sector in Neiva”, however in the haplotype network is possible to see that H18 is also present in Cauca River lower sector and San Jorge River. I strongly recommend giving the information based on individual than haplotype.


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: MEIOFAUNAL COMMUNITIES AND NEMATODE DIVERSITY CHARACTERIZING THE SECCA DELLE FUMOSE SHALLOW VENT AREA (GULF OF NAPLES, ITALY)
Review round: 1
Reviewer: 1

Output:
Basic reporting: The paper is about the characterization of meiofauna community in shallow hydrothermal vent in the gulf of Naples. The argument appears original an the work deserves to be published, but several inconsistences and corrections must be made before. Several concerns emerged by the images and table formatting. The numeration of figures as reported in the MS does not reflect the actual numeration of the single images reported at the end of the manuscript. The captions must be reformulated to be more informative in cases the images and tables are extrapolated by the text (they should be autoinformative). Problems with some references formatting emerged as well. Moreover, it seems that conclusion is lacking.
Experimental design: The experimental design is good for the questions the authors wanted to give an answer. The sampling appears rigorous as well. The analyses performed are quite standard and well applied.
Validity of the findings: Following the good experimental design, also the findings are valid and well interpreted.
Additional comments: Following I report several points that the author should modify.
Introduction
Line: 85: a dot at the end of the sentence seems to lack. “…for this taxon. However….”
Lines 112-122: Please move this part to the study area description or to the discussion. In the introduction report only the background problem of study shallow vents.
Material and Methods
Lines 139-144: move all this part to the sampling strategy.
Line 147: delete the reference as it is useless.
Lines 148-149: can you specify how did you collect the sediment? By scuba diving or what else?
Data analysis.
I would rearrange all this part according to the following suggestions:
Line 189: at the end of the sentence, please report “Faunal data were log(x+1) transformed and analysed using tests based on Bray-Curtis similarity matrices (multivariate analyses) and Euclidean similarity matrices (univariate analyses).”. Delete the lines 197-198 afterwards.
Lines 192-193: move this sentence after the Permanova description one. Moreover, change the sentence as “Pair-wise tests were carried out to verify the significance of the differences among sites and layers if any were observed in the main test.”.
Line 200: at the end of the sentence add “….(using 70% as cut-off) to determine the contributions of each species (cit).”. Delete lines 202-204 (comprising the sentence “This analysis of dissimilarities…”.
Line 201: delete between brackets “e.g. based…” leave only the reference.
Line 205: can you provide more info about the cluster technique you adopted? K-means? UPGMA?
Line 207: delete for.
Lines 209-217: something went wrong with the rows formatting.
Line 208: after brackets write “with a forward selection of the independent variables and 4999 permutations of residuals”. Delete lines 212-218.
Line 219: write “All the analyses were carried out by means of the software….”.
Results.
Lines 223-235: are these analyses made by you or by Donnarumma et al? If the last is true, please report these info in the study area paragraph and report in here only your own results.
Line 240: at least the first time please what the numbers are. For example, 1142±713.8 ind/cm2 (mean ± standard error, hereafter). Check the figure numbers reported in the MS. There is not a fig 2a. Check all the figure numeration all along the text and be consistent with actual figure numbers.
Line 244: delete (Permanova, not significant) you already said it was not significant, it is a useless repetition. Report just the table where one can found the test. It is easier for the reader. Moreover, in the tables report the actual p value to give the readers the possibility to interpret on their own the statistical significance of the test, above all in these times of “significance” meaning debate.
Line 247: delete these brackets, here and all along the MS.
Line 252: what the numbers are? Please report the units.
Lines 253-255: In this sentence saying that the site was the most important factor is not totally correct. In tests like this, with interactions, the interaction itself is the most important (although this terminology is inappropriate), and you, as a rule of thumb, must be look first at that term. Sometimes you can even ignore the significance of the single term significance in case the interaction is significant. So, discuss the interaction and the corresponding pairwise, rather than the single term.
Line 256: in brackets report the actual p value. Better, report the pairwise in the same table of the main tests or in a separate table. This applies for all the pairwise in the MS.
Line 262: check figure.
Line 265: change “was” with “were”.
Line 284: again report actual p value or table, hereafter.
Lines 295-296: The ANOSIM Is not reported in the MM. I suggest to delete this sentence, even because the results are redundant with PERMANOVA.
Line 298: I don’t understand which is the correspondent figure 5.
Lines 317-319: Here it is not clear if the main test is reported or the pairwise. If the last is true, where the main test is?
Line 328: Something went wrong with table 3 formatting please reduce the width of the columns to be sure the entire table is within the margins.
Discussion
Line 350: close brackets after 2016.
Line 544: A summary of the conclusion is lacking. Can you summarize all the findings and their ecological importance in a proper paragraph?
References
Check the formatting of the references of the following lines: 613, 649. The journal names should be in italic. Make a general check of the PeerJ formatting standards all along the MS. I suggest for references to use bibliographic software.
Figure and table captions.
Please, be sure to report the legend for all terms in the figures and tables. Imagine the figures as standalone products that should be auto informative if extrapolated from the MS.
Figure 1: I don’t like this image, but I understand you wanted to maintain it because it is part of complex work and was reported also in Donnarumma et al. But at least, give a more detailed description of the image. For example, does the image be captured with a probe like a scan sonar or what else?
Figure 9 caption: please delete “DistLM (distance-based linear model)” report only “dbRDA canonical model….”. Moreover, what do the segments correspond to? Correlations (Pearson or Spearman) with axes? Or what else? Same comments for the next figure 10.


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: MEIOFAUNAL COMMUNITIES AND NEMATODE DIVERSITY CHARACTERIZING THE SECCA DELLE FUMOSE SHALLOW VENT AREA (GULF OF NAPLES, ITALY)
Review round: 1
Reviewer: 2

Output:
Basic reporting: Clear and unambiguous, however further check is needed for consitency and definitions (see comments below).
Literature references, sufficient field background/context provided.
Professional article structure, figures, tables. Raw data shared.
Self-contained with relevant results to hypotheses.
Experimental design: Original primary research.
Research question well defined, relevant and meaningful.
Original and novel.
Rigorous investigation performed to a high technical and ethical standard.
Methods described with sufficient detail and information to replicate.
Validity of the findings: All underlying data have been provided; they are robust, statistically sound and controlled.
Conclusions are well stated, linked to original research question and limited to supporting results.
Additional comments: General comments
The paper provides new insight on a very interesting ecological aspect which has been also poorly investigated so far. In addition, the experimental design and the data treatment are rigorous and ecologically sounding. So that, this article could be very interesting for the wide audience of PeerJ. However, I suggest to the Authors to carefully check the entire ms, since I am confident that it could be even ameliorated. First of all, I suggest to check the entire ms for consistency. Authors should maintain the same logic flow throughout the whole ms. More specifically, they should talk about characteristics of meiofaunal assemblages in shallow vs deep vents, characteristics of nematode assemblages in shallow vs deep vents, at genera and species level, and meiofauna vs macrofauna in vents. When they talk about “diversity” they should explore first the “level of biodiversity”, in terms of richness of taxa and diversity indexes, and then explore the putative differences in taxonomic composition. Following this scheme, they would avoid the missing of some important information (see comment on the Discussion section below). I would suggest also to revise and check the terms used throughout the ms, first for their definition in theoretical ecology (e.g., definition of “population”) and then for their consistency throughout the entire ms. This could help the reader in following the logical framework.
Below my specific comments.

Introduction
The Introduction is well written and quite clear, but maybe could be simplified in some parts. Some paragraphs seem very detailed and the specific information could be reported in the Discussion section. See as example, lines 83-88.
Line 103. A population is composed by individuals belonging all to the same species. I would change into “assemblage” and use the terms “assemblage” throughout the entire ms.
Lines 83-88 and 114-122. I would move this paragraphs to the Discussion section. The Introduction should just present the ecological problem and hypothesis and not provide all the available information.

Methods
It is unclear how sediment cores have been collected. By scuba diving?
Line 145. Those described are sampling methods and not strategy. The sampling strategy has been already described in the previous paragraph.
Line 165. “Until” indicates a temporal sequence.
Line 171. I would use “site” instead “station”, in order to be consistent throughout the entire ms.

Data analysis
Line 190. “Descriptors of meiofauna and nematode assemblage composition” is unclear. Which are they? And more specifically, which are the descriptors of assemblage composition?
Line 192: Pair wise tests are not for verifying the significance of differences, but to ascertain specifically between which samples the significant differences are.
Line 195. I suggest to calculate the diversity indexes cumulatively for the 3 replicates and describe the pattern, avoiding the statistical analysis. Indeed, using separatly the replicates could be misleading in the idenx caluclation, since in this way the index do not consider the species in common/exclusive among the 3 replicates. So that, the results of the statistical tests could be deviated. Otherwise, I suggest to maintain both approaches (expressing the indexes as avg+st.dev carrying out statistical tests and calculating them also cumulatively).
Line 196. Replace “communities” with “assemblages”.
Line 207. Replace “community composition” with “species composition”.
Line 211. Replace “diversity and community composition” with “richness of taxa and taxonomic composition”. The term “diversity” is too vague here, it is unclear what Authors are referring to. According to the ecological definition of “community” (different species living in the same area), meiofauna are not a community (because meiofauna are not identified at species level), rather an assemblage.
Line 212. Please, replace with “nematode trophic diversity and life strategies”.
Line 218. PCA has not been performed in this paper. Maybe dbRDA? Also ANOSIM is missing here? Please, check.

Results
Line 229. Why temperature is not expressed as avg±st.dev. here?
Line 232. Maybe “surrounding environment” is better?
Line 237. “Meiofauna abundance, community composition and distribution”. Please, replace with “taxonomic composition”.
Line 238. How a composition can be reported in a table? I would say "abundance of each taxon".
Line 241. As far as I understood these differences are not statistically significant.
Line 249. “5_10”? I would use 5-10 cm, as in other sections of the doc.
Line 252. See comment above on the diversity indexes. Same for the richness of meiofaunal taxa.
Line 257. Please, use “taxonomic composition” instead of “community structure”.
Line 271. What Authors mean with “frequently”?
Line 281. Please, indicate “µg C” only once.
Line 286. At all sites? And maybe is “going deeper”.
Line 288. Never heard about “Nematode structural indices”. It has no sense. MI indicates life strategies and not functional diversity.
Line 323. “Faunal descriptors (i.e., meiofauna abundance, community composition, number of major taxa,”. The term “descriptor” is not common, above all for community composition (which should be “taxonomic composition”).
Line 327. Personally, I do not like the term “nematofauna” because it could comprise also macrobenthic nematodes. However, I recognize that it is matter of personal opinion.

Discussion
Line 339. I think that hydrothermal vents are not biotopes.
Line 358. Please, replace “density” with “abundance”.
Line 359. Please, replace “abundance” with “amount” or “quantitative”.
Line 366. Only in Mediterranean Sea?
Line 370-371. Both in vents and no-vents systems?
Line 384. Again, the differences are not significant.
Line 405. The term “permanent” is not appropriate, since no temporal analyses have been conducted.
Line 409. Are only living forams here?
Line 404. What about other meiofaunal taxa? There is any exclusive taxon at each site?
Line 438. Please, do not use “populations”.
Line 503. Where correlation analysis has been carried out?
Line 543. Replace “community with “assemblage”.

Figures and Tables
Figure 1. What are “white” and “yellow” vents?
Figure 5 and 6. To my knowledge chaetognata are planktonic. Copepoda and nauplii should be merged together, being the same taxon.
Table 2. What does it means “All replicates are reported”?. I guess the avg is reported? Or cumulative indexes?
Table 3. I guess Var% is not expressed in 100. Otherwise the values are too low.


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: MEIOFAUNAL COMMUNITIES AND NEMATODE DIVERSITY CHARACTERIZING THE SECCA DELLE FUMOSE SHALLOW VENT AREA (GULF OF NAPLES, ITALY)
Review round: 1
Reviewer: 3

Output:
Basic reporting: This manuscript reported the meiofauna, especially marine nematodes communities around a hydrothermal vent in the shallow water. Generally, the materials and methods are suitable. The results are reliable and the manuscript was well organized and written.
Experimental design: There are totally four sites selected for meiofaunal and nematodes samples collecting with different distances to the vent. This experimental design is suitable to reflect the effect of hydrothermal vent on meiofaunal and nematodes communities. The laboratory processing and data analysis are both OK.
Validity of the findings: The findings of this study are reliable based on the data presentation.
Additional comments: I have two suggestions for the improvement of the manuscript.
(1) Figure 1 is not clear and not friendly for readers.
(2) The methods to collect meiofaunal samples are not clear. By remote sediment corers or by diving or by submersibles/ROV? Please state it clearly.


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: MEIOFAUNAL COMMUNITIES AND NEMATODE DIVERSITY CHARACTERIZING THE SECCA DELLE FUMOSE SHALLOW VENT AREA (GULF OF NAPLES, ITALY)
Review round: 2
Reviewer: 1

Output:
Basic reporting: After the three reviewers suggestions the MS greatly improved. Now the text is clearer and fluent. I observed some mistyping but I suggest to the editor not to resubmit the manuscript by the authors but to have them corrected during the proofs revision by the authors themselves.

These are the mistyping:
Line 50: Extra space at the beggining of the sentence.
Line 74: the same as for line 50.
Line 195: please change Log(x+1)[(x+1) as subscript] with log(x+1).

I accept all the corrections made by the authors that diligently followed my and other reviewers suggestions.
Experimental design: I already stated in the first review that the experimental design is good for the questions the authors wanted to answer.
Validity of the findings: As stated in the first review, the findings are valid and relevant.
Additional comments: I congratulate the authors for the good work made.


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: MEIOFAUNAL COMMUNITIES AND NEMATODE DIVERSITY CHARACTERIZING THE SECCA DELLE FUMOSE SHALLOW VENT AREA (GULF OF NAPLES, ITALY)
Review round: 2
Reviewer: 2

Output:
Basic reporting: The manuscript has been improved, considering almost all the suggested comments.
Experimental design: The requested details have been added.
Validity of the findings: The validity has been recognized at the first stage of the submission.
Additional comments: Overall, the manuscript has been improved, considering almost all the suggested comments.

In some cases, Authors did not accept the suggestions (e.g., keeping separated different life stages even belonging to the same taxa or calculating the diversity indexes. I am still convinced that these are errors, from an ecological point of view, but I recognize that it is matter of personal opinion.
I think also that at the end the Scientific Community will evaluate the paper, citing it or not.


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: MEIOFAUNAL COMMUNITIES AND NEMATODE DIVERSITY CHARACTERIZING THE SECCA DELLE FUMOSE SHALLOW VENT AREA (GULF OF NAPLES, ITALY)
Review round: 2
Reviewer: 3

Output:
Basic reporting: This manuscript has been improved significantly after revision.
Experimental design: no comment.
Validity of the findings: no comment.
Additional comments: This manuscript has been improved significantly after revision. It should be acceptable for publication.


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

Input:
Title: PROLIFERATING ACTIVITY IN A BRYOZOAN LOPHOPHORE
Review round: 1
Reviewer: 1

Output:
Basic reporting: In their article entitled "Proliferating activity in a bryozoan lophophore: a case study in gymnolaemates“ Shunatova and Borisenko describe the occurence of proliferating cells in the lophophores of three species of gymnolaemate bryozoans. Proliferating cells were visualised by incorporation of labeled nucleotide analogues and imaged using confocal microscopy. In addition the fine structure of the lophophores and the tentacle bases was described in the same plus one additional species. This investigation is very interesting, because patterns of cell division during growth and organ formation in bryozoans have so far not been studied. The results can help explaining how different lophophore shapes arise within a colony and how regeneration happens.

The language needs much improvement. The text is full of errors and typos. The most common mistakes concern the use of articles and prepositions, tense, as well as singular and plural forms. I have examplary made corrections in the abstract and on the first page of the Introduction secions, but can not fulfil this for the whole manuscript.

The topic is introduced and set into context of the existing literature. Some gaps concern the references of stem cells and proliferation in other animal groups (indicated in the pdf). Also, the use of the term "stem-like cell“ is not clear to me. I have so far only seen this term used for cancer stem cells. If you use this term here you should very clearly define what it means, and how it differs from "stem cell“. Otherwise I would recommend using the latter.

The figures provided are of high quality. They illustrate very well the findings and complement the descriptions given in the results section. Figure 4 is a bit difficult to understand, because the coloration for vertical and horizontal planes don’t make sense in the perspective drawing. I would recommend here to simply remove the lower green part, or to put two drawings side by side, one showing a horizontal plane, the other a vertical plane
Experimental design: The methods chosen are appropriate and described in sufficient details. I can see no major flaws.
Validity of the findings: The descriptions of the ultrastructure are very detailed and thoroughly discusse. the finding of a deuterosome is indeed interesting and worth to be reported, even if comparative data are scarce.

One point that remains a bit more elusive is the fate of the proliferating cells, both during normal growth as well as regeneration. To clearly show cell fates and the potency of the supposed stem cells, more EdU experiments with pulse-chase treatments are neccessary. However, these can be extensive, so the authors might want to consider this for a follow-up study. For this study I would simply recommend wording their interpretations in lines 399-409 a bit more careful (e.g. avoid "absolutely sure“ and such expressions.
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: PROLIFERATING ACTIVITY IN A BRYOZOAN LOPHOPHORE
Review round: 1
Reviewer: 2

Output:
Basic reporting: English is good
Literature references are mostly sufficient
Row data of confocal sudy are NOT shared (!)
Interesting hypotheses and results
Experimental design: The primary research is original
experimental design is well done
Validity of the findings: no comment
Additional comments: The study is devoted to comprehensive investigation of the tentacle apparatus of four bryozoans species. The study is done with the use of all modern zoological methods, which allow to obtain very interesting new results. This study contains perfect photographs and many schemes. The study may be published in “PeerJ” after correction, accordingly to the list below.
Major comments:
1) In current version, the Introduction consists of several parts, which seem to be disconnected with each other. It would be better to organize the Introduction in logical way.
I recommend authors to start the Introduction from the description of bryozoans, their anatomy, phylogeny, and some peculiarities of life style and feeding. Then, mention why the proliferating activity is important for these animals and how the proliferating activity is studied at this moment concerning bryozoans and other animals. After all, to formulate the problem of the study.
2) In Material and methods, define the chapter “Animals” (or “Collection of animals”) where provide all information concerning name of species, place of their collection, methods f collections, ect.
3) Because most of results are devoted to organization of the tentacles and lophophore of several bryozoan species, the title of the paper needs some correction. Nine of twelve figures of the manuscript are devoted to the description of the organization of the lophophore and tentacles! To my mind, the information about organization of the lophophore must be incorporated into title of the manuscript.
It is difficult to recommend something and authors know better how to change the title…. I can recommend following variants: “Organization and proliferating activity of the lophophore….” “Fine structure and….”, “Details of morphology and ….”.
4) I recommend authors to prepare scheme or (better) 3D reconstruction of the lophophore base, in which the tentacles and ciliated pits must be shown. It is important for better understanding of morphology of the lophophore base. Thus, this scheme may allow reader to understand the location of the ciliated pits in respect to the tentacles and the mouth.
5) Some important recommendations for preparation of figures must be accepted

Minor comments:
P.7, L. 59 “gut and associated muscles and nervous system” must be changed to “gut and associated muscles, and nervous system”
P.7, L. 74 “….and, correspondingly, and….” must be changed
P. 8, L. 110. “At the bases tentacles unite and…” replace to “At the bases, tentacles unite each other and….”
P. 8, L. 119-120. Please provide the references for phrase “It is well known that different benthic animals predate on bryozoans and usually they consume a whole polypide or considerable part of it.”
P. 9, L. 144. “Aquiloniella scabra van Beneden, 1848 and..” replace to “Aquiloniella scabra van Beneden, 1848, and…”
P. 9, L. 146. “E. pilosa and A. scabra…” replace to “E. pilosa, and A. scabra….”
P. 9, L. 161. Please provide the name and label of the tool, with which the semithin and ultrathin sections were done.
P. 10, L. 202. “Rhamphostomella ovata and Aquiloniella scabra.” replace to “Rhamphostomella ovata, and Aquiloniella scabra.”
P. 11, L. 231. “At the very base of the tentacle…” – “very base” sounds wrong. Please rephrase. Use the term “the most proximal”
P. 12, L. 285. See my previous comment
Figures are very nice. But in some pictures, the abbreviations are not properly visible. I recommend authors to use “Stroke” tool for some abbreviations (for ex., “fc” 1D; “1µm”, “ar”, “ECM, “k” in Fig. 5; “m”, “k”, “dG” in Fig. 6 and many others).
It looks very negligently the location of the scale bar in different parts of photos within one plate. Please use the similar location of the scale bar at least in one plate.
Different size of abbreviations is used for different figures. For example the size of scale bar calibration is much bigger in Fig. 12. I recommend to use the same size for same types of abbreviations through all figures.


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: PROLIFERATING ACTIVITY IN A BRYOZOAN LOPHOPHORE
Review round: 1
Reviewer: 3

Output:
Basic reporting: Shunatova and Borisenko have followed the PeerJ instructions to authors in formatting their paper. The authors have provided sufficient information in the introduction to provide readers with an understanding of bryozoan zooid anatomy and colony structure.  The authors make good use of the existing literature to provide context for their study as it relates to bryozoans and to the broader biology of animals.  The figures the authors include in the manuscript beautifully illustrate the data they describe in the results section, although some may find figure 4 difficult to interpret. The work the authors present in this manuscript is an appropriate unit of publication, although it is clear that the results presented in this submission fit into a broader research program, which will yield other publications on the structure of bryozoan polypides. Overall the paper conforms to professional standards, but there are a number of typos and grammatical mistakes, requiring that the manuscript be carefully proofread. For example, line 48: contributes should be contribute; line 49: cells should be cell; line 64: In majority should be in the majority; line 65: regenerate should be regenerates; line 73: the latter are arranged in five longitudinal rows and, correspondingly, and form five ciliary bands should be the latter are arranged in five longitudinal rows and correspond to five ciliary bands; line 131: technic should be technique; line 252: an should be the; line 272: Goldgi should be Golgi; line 298: Cell membrane should be The cell membrane; line 324: cells in per should be cells per; line 324: posistive should be positive; line 349: is higher under the operated tentacles should be was greater at the base of the wounded tentacles; lines 454 and 481: Recent should be A recent. In addition, there are many places in the text where a different word should be used.  For example, line 84: Depleted should Exhalent; line 114: registered should be reported; line 119: mentioning should be report; line 229: up to three should be from two to three; line 306: Basing should be Based; lines 342, 343, 350-352, 457, 463: operation should be surgery; line 356: comparing should be compared; line 373: Basing should be Based; line 402: comparing should be compared.

Missing references – on lines 454 and 481, the authors refer to recent studies, but do not cite a reference.
Experimental design: The research the authors present in this manuscript has three parts.  First, the authors investigated the organization and cell structure of the tentacles, lophophore base, and the ciliated pits in four different species of gymnolaemate bryozoans (Rhamphostomella ovata, Electra pilosa, Aquiloniella scabra and Eucratea loricata) using semi-thin sections, TEM, and SEM. Second, the authors identified regions of actively dividing cells in lophophores at different stages of development (i.e., age) in R. ovata, E. pilosa, A. scabra by using a thymidine analog (EdU) to label replicating DNA which the authors imaged using a confocal microscope after chemically attaching the fluorochrome Cy5 to the incorporated analog.  Lastly, the authors used their method of identify dividing cells to evaluate the contribution of cell proliferation to wound healing in surgically injured tentacles of Electra pilosa. The data the authors present in this manuscript represent a significant contribution to our understanding of the bryozoan lophophore and animal cell structure. The methods the authors used are appropriate for their investigations, mostly clearly written, and sufficiently detailed for the work to be repeated. However, the authors may have biased the labeling of dividing cells to those cells with a relatively short cell cycle by using a labeling time of only six hours. For example, a labeling period of six hours is unlikely to detect cells that divide on the time scale of once every 3-4 days or once per week, particularly if the mitotic index of the cells in that region is low.
Validity of the findings: Findings on the organization and cell structure of the tentacles, lophophore base, and the ciliated pits

The authors provide a very good set of descriptions of the cellular structure of the tentacles, lophophore base, and ciliated pits for the four species they studied. Their observations on the cells of ciliated pit are of particular importance because this structure within the lophophore has been an understudied feature of bryozoans.

Findings on the regions of actively dividing cells in lophophores at different stages of development

The authors set out to collect data on cell division in the lophophore to evaluate “the hypothesis that tentacle growth/elongation is intercalary and cells’ proliferation takes place somewhere at the lophophore base because such pattern makes tentacle elongation possible without interrupting of the feeding process.” (lines 133-135).

In addition to the text from lines 133-135, the authors refer to the growth/elongation of the tentacles as being “intercalary”, see below.  However, it is not clear to me what the authors are referring to as the hypothesis of intercalary tentacle growth.

Lines 34-37 This confirmed the suggested hypothesis about intercalary tentacle growth which provides a potential to alter a lophophore shape in adult polypides according to rearrangement of colony wide water currents during colony astogeny.

Lines 389-39: These patterns together with the absence of proliferating cells in the tentacles of adult polypides demonstrate early specialization of ciliated cells and provide evidence for intercalary growth of tentacles.

Lines 481-481 Recent study demonstrates that the specific design of bryozoan lophophore base enable intercalary growth of tentacles.

There are several other elements pertaining to the authors’ findings on dividing cells that require change or clarification:

a. The authors categorize the lophophores they examined as “young bud”, “late bud”, “young polypide”, and “adult or old polypide”. Young and late bud stages are developmental stages before the polypide is fully functional and depending on the size of the lophophore, I would expect that it is relatively easy to compare similar stages across the three species they examined. To stage young and adult polypides, the authors use zooid position within the colony relative to the growth margin. To identify these relative positions the authors use the term “generation”, with younger generations located closer to the growth margin.  This terminology is confusing.  First, the series of asexually budded zooids in a bryozoan colony are not usually referred to as different generations, because they represent clones of the same sexually produced ancestrula.  Second, the numbering system is counter to what we normally think about in terms of generational ages (i.e., the 1st generation comes before the second generation). I would suggest that the authors consider just using the relative positions of zooids to the growth margin to estimate the “age class” of a polypide. In addition, the authors refer to some young polypides as “fully developed” which is not defined  or distinguished from just young polypides (e.g., line 321).

b. A second concern is the actual “developmental age” of a lophophore relative to the position of its zooid in the colony. The authors state in lines 149-152 that “We numbered zooid generation starting from the colony edge and took into account only fully developed and actively feeding polypides, we did not consider buds.” I assume this means that the authors did not start their numbering system until they reached a point in the colony that was proximal to the growth margin and any zooids without an extended lophophore. The three species the authors examined have very different colony forms and I would expect very different rates of colony growth.  For example, E. pilosa forms colonies that are lightly calcified, encrusting sheets; A. scabra forms colonies that are lightly calcified, biserial, and erect; and R. ovata forms colonies that are highly calcified and encrusting.  The authors aging system may work well for comparisons within a colony or species, but it may be inappropriate for comparisons across the three species. For example, the distributions of EdU positive cells shown in figure 11 for young polypides of A. scabra and R. ovata are very different than that shown for a young polypide of E. pilosa. Is this a difference among species or age of lophophores? I recognize that the authors are doing their best to control for polypide age, but it might be helpful if the authors explicitly address this question as they describe their methods.

c. Variation in EdU-positive cells and Statistical analysis – on lines 324-327, the authors state for young fully developed polypides, “We registered from 8 up to 14 EdU-posistive cells in per ciliated pit. This parameter varies across ciliated pits and across polypides of the same generation for each studied species.” On lines 334-336, the authors state, “Though our study is qualitative and we did statistically analyze the proliferating activity at the lophophore base, the number of EdU-positive cells per ciliated pit in ‘old’ polypides is less than in ‘young’ ones (especially in E. pilosa): from 0 up to 4. Lastly, on lines 466-468, the authors state, “We did not statistically analyze the proliferating activity at the lophophore base since our study is qualitative and this is the first attempt to check the ability of tentacle regeneration in marine bryozoans.” I would agree with this last statement, that the authors did not actually statistically analyze the data. However, I think it is important that the authors provide at least some minimal additional information about the variation of EdU-positive cells in young and old polypides of each species, including sample size, mean, and some error term, such as standard deviation or standard error of the mean.

d. The authors present data that is clearly suggestive that cells of the ciliated pits and oral regions contribute to the growth of the tentacles.  However, their data does not include definitive evidence that 1) EdU-labeled cells of the ciliated pits or oral region are incorporated into the tentacles or 2) the tentacles of the adult polypides they examined had grown (either increased in length or cell number) compared to the tentacles of the young polypides they examined. Consequently, the authors may want to be more careful in presenting and interpreting their data. For example:

Lines 337-338 – “The larger number of EdU-positive cells in ‘young’ polypides demonstrates that their tentacle still lengthen until their lophophores acquire a specific shape.”

Lines 397-399, “We are absolutely sure that CP- and DP-cells give C- and D-cells correspondingly since we traced stages of kinetosome biogenesis in these multiciliated cells.”

Lines 406-407 – “This study revealed the possible function of ciliated pits: they are responsible for tentacle elongation in young and adult polypides.”

e. The authors report a difference in the number of EdU-positive cells in the ciliated pits of young and adult lophophores (lines 324 and 336). However, it is not clear from the manuscript whether their description of ciliated pit organization and cell structure in lines 228-305 is based on studies of young and/or adult polypides. It would be interesting to know if the organization and/or cell structure of the ciliated pit differs between young and adult lophophores.

f. The authors demonstrate that during development, the cells of the lophophore that can be labeled with EdU in a six hour period become restricted to the ciliated pits and the base of the lophophore.  The authors interpret regions of the lophophore without EdU-positive cells after a six hour labeling period as regions where cell division does not occur.  However, extending the labeling period may detect slower dividing cells in other regions. Even the authors extended the labeling time to six hours to improve the EdU-positive signal in adult polypides (lines 311-312).

Findings on the contribution of cell proliferation to wound healing in surgically injured tentacles of Electra pilosa

The authors investigated if tentacles of E. pilosa regenerated after a piece of the distal end was surgically removed. The authors observed no regeneration over a seven-day period. Six hour incubations in EdU, labeled few cells in the tentacles, but did include an E-cell near the wounding site and a cell of the tentacle coelomic lining. The authors report an increase in EdU-positive cells in ciliated pits at the bases of the injured tentacles.
Additional comments: The caption for figure 12 does not identify the time after surgery for G. I believe the figures 12E-G are all 120 hours after surgery.


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: PROLIFERATING ACTIVITY IN A BRYOZOAN LOPHOPHORE
Review round: 2
Reviewer: 1

Output:
Basic reporting: The text has much improved compared to the previous version. The authors have done a very good job incorporating most of the reviewers' comments. The language has improved. Although there are still few minor shortcomings, I am confident these can easily be addressed by a thorough typesetting. I have no further concerns or objections and can recommend publication of this manuscript. All positive comments given in my initial review still apply.

Some minor typos/errors I have picked up on the way:
124	‘predate’ should be changed to ‘prey’
133	‘basing’ should read ‘based’
168	‘was’ should be ‘were’
374	‘that’ should be ‘those’
475	I think you mean your study? Then change ‘A recent’ to ‘This’. Otherwise provide reference…
502	same as the above comment
Experimental design: OK, as previously reported
Validity of the findings: Also still OK, comments in this direction made by reviewer 3 and myself have adequately been dealt with
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: FUTURE SEA-LEVEL RISE DRIVES ROCKY INTERTIDAL HABITAT LOSS AND BENTHIC COMMUNITY CHANGE
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is well written and easy to read for the most part (see comments below).
Experimental design: I don't understand the formula used to calculate the densities of the invertebrates. Why is the density calculated across the total intertidal area? Please explain.

 the language in the methods should be simplified and less jargon. E.g. landscape surface area? species stratified random point count?

I strongly disagree with the decision not to consider density dependence. The end result is that for some species density was increased by 2 to 5 times! Intuitively this doesn't make any sense unless there is a fundamental shift in the underlying ecology - or on a metabolic scale, a fundamental shift in the thermodynamics that would allow organisms to become more efficient and therefore be able to survive at higher densities. There is no evidence to suggest SLR will do either. Surely the better option would have been to assume that density would always be roughly similiar to present day conditions regardless of the amount of SLR?
Validity of the findings: It is unclear how the findings of this study fit within a broader context. While the models appear to show a substantial decrease in the availability of habitat for low and middle intertidal species, the true impact of this on their populations are less clear. For instance, low intertidal species may also be perfectly happy growing subtidally, so they may actually get more habitat overall if rock platforms become permanently submerged. Its not clear whether loss of habitat at the scale that the authors measured will have any meaningful impact on populations overall. While there may be habitat loss in some locales, there could be more habitat opened up at other locations - so the overall change in the amount of habitat available for a species is overall relatively unchanged. Yes this may have important implications for local populations - particularly when thinking about the scale of marine protected areas, for instance - but overall what are the impacts likely to be. I'd like to see the authors comment on the importance of scale when considering SLR impacts.

Although the authors briefly mention the possibility, too little is made of the potential for erosion and other geological processes to play a role in the amount of habitat that will be available under different SLR scenarios. Is it possible that in the region where this study was done SLR will result in larger/wider rocky platforms as rising waters erode softer materials at the base of cliffs, and leave the harder rocky platform? Perhaps some more information about the geological characteristics of the study sites may provide greater context for the non-American reader and support the implied assumption by the authors that erosion will be essentially zero under various SLR scenarios.

In the discussion, the authors do not cite any other papers that have examined the effects of SLR on marine communities. The authors need to compare and contrast their results with the results from previous studies. Are there broader/global trends? Are the impacts of SLR site specific?
Additional comments: The figure captions need to be improved. For instance the legends are not explained. What are SCR0, CNM1, CNM2, CNM3?

Through-out discussion: Redundancy is an issue e.g. "could potentially" - it makes it seem as if the authors are not convinced about what they are saying.


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: FUTURE SEA-LEVEL RISE DRIVES ROCKY INTERTIDAL HABITAT LOSS AND BENTHIC COMMUNITY CHANGE
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript was well written with appropriate literature references. There are some minor grammatical issues in the attached document.
Experimental design: There are a number of issues with the design that I have concerns about. If these issues cannot be clarified or resolved, the manuscript either needs to be greatly reduced with a focus on less specific patterns with clear statements of the limitations of the study or the manuscript should be rejected. The issues include:
1.	The area of the rocky intertidal zone estimated in this study is the horizontal area, not taking into account the vertical relief. This needs to be clearly stated and the implications of this limitation discussed.
2.	The authors limited their study to the Highest Atmospheric Tide (HAT). As I understand the study, this is a large deficiency in the design that greatly affects the conclusions of the study. It seems that if the authors are modelling a 2 m increase in SL, then they should have mapped out the area at least 2 m above the HAT. By limiting to HAT, they are artificially constraining the top end of tidal heights when modelling under future SLR scenarios. For example, at SCR, the maximum tidal height mapped out was a HAT of 2.177, thus a 0.0 to 2.177 tidal range. When modelling a 2.0 m SLR, this now constrains the intertidal zone in the future to a 0.0 to 0.177 m range (HAT is currently 2.177 - 2.0 m SLR = 0.177 max tidal height in the map, constrained on the lower end at MLLW of 0.0 m). The upper end of the upper intertidal zone will extend much further past what the authors have modelled (upper zone currently extends to 1.6 m at SCR thus a 2.0 m SLR means the upper end will extend to the current equivalent of 3.6 m, ~1.5 m above there area mapped out). The authors did not establish what is past the HAT which, at some of the sites, includes some gently sloping rocky habitat. If the habitat above the HAT is sandy beach, it is likely that the sand will be transported out of the system, exposing the rocky habitat underneath. If there is a vertical wall past the HAT, the vertical habitat will be used by intertidal organisms, although the tidal gradient will be greatly “squeezed”; but that is not included in the model. Although difficult to model, a vertical wall will also erode as the sea level rises slowly over time thus establishing more horizontal surface where tidal zones can extend into. This also was not discussed. I believe the limitations to the design (only mapping to HAT) severely reduces the value of the study and, unless a strong rebuttal is provided by the authors, suggest this paper should not be published. At minimum, in the light of the design issues, the specific conclusions of the study should be greatly reduced and the large number of limitations clearly stated.
3.	I had a number of issues with the biological sampling procedure and data usage. First, the authors need to define “benthic space occupiers”. This typically describes the organisms attached to the rock. However, Egregia and Silvetia, for example, only attaches to the rock in a pretty small area but the seaweed itself can cover large areas of rock during low tide due to its length. From pictures, you can only see the seaweed canopies in these scenarios, not the benthic space occupiers that are underneath. Second, there are problems associated with the identification of species listed in S2 with species either misidentified or grouped incorrectly. See the document for a specific list. While most of the misidentifications do not necessarily alter the general patterns describe (e.g. misidentification of chitons as Katharina spp. doesn’t change the fact that a different genus of chiton will decline in the future), they do raise some concerns about the authors familiarity with the system. Third, assessments of the biological communities are limited to the horizontal surface and this should be clearly stated. Because of this, percent cover estimates are acceptable (again, assuming the limitations of horizontal surface sampling stated) but I do not believe species counts are valuable here, particularly for some of the target species for density analyses. Many of the target species are hard to count as they are in cracks and crevices, in the mussel matrix, underneath seaweeds, etc. Even in the field, counting some of these organisms is difficult; utilizing photos to make these counts are likely to be highly inaccurate. Hiding is likely to be even more evident for some of the species on the upper tidal zone edge of their tidal distribution (as they attempt to minimize desiccation stress) thus the upper tidal limits of these species measured in this study is likely incorrect.
4.	I do not have a lot of faith in the accuracy of the biological data because of the issues raised above. What the authors might be better off doing is choosing a set of taxa that create clear zonal trends at the sites (on a horizontal level), probably sticking to species that tend to clump together (e.g. surfgrass, mussels, red algal turfs, rockweeds, Tetraclita barnacles, acorn barnacles) and are easy to distinguish in photos. The authors can then determine the tidal range of these populations (upper and lower tidal extents), followed by modelling similar to what the authors conducted for the different zones (high, mid, low). The authors appeared to do this with the entire species list but many of these taxa are not really limited to any particular zone. For example, Ulva, green algal turfs, Petalonia, and Phragmatopoma often establish in disturbed areas or, being opportunistic species, establish for short periods of time here are there throughout the intertidal zone (regardless of tidal height). In this case, SLR is not going to act the same on those taxa as compared to those that clearly establish within a species tidal zone. Other taxa are typically limited to pools (e.g. Sargassum, Anthopleura sola) which you cannot really model here.
5.	The section on “Impacts of SLR to benthic cover”: The authors used the term “cover” through the paragraph but they are actually referring to area or aerial extent, not cover. The area was reported to decrease for numerous taxa with future SLR scenarios, not surprising given the area of the rocky intertidal as a whole decreased with SLR. By cover (%) is a different parameter and the patterns described are not necessarily true. For example, for ease of of describing the patterns, let us say that at SCR, 100% of the middle intertidal zone is rockweeds. With 45% of the site being middle intertidal zone, that means that the site is 45% rockweeds. At the 1.0 SLR scenario, the middle zone is now ~60% of the site thus a mid zone of 100% rockweeds will now cause rockweeds to make up 60% of the site in the future. Change the discussion of “cover” in this paragraph to area.
Validity of the findings: Given the issues mentioned in review of the experimental design in section 2, it is difficult to grasp how much of the conclusion are valid.

It was stated on page 18, Lines 382-383 “Our results suggest that lower and middle intertidal species will generally experience the greatest losses of benthic cover and abundance.” Assuming all of your patterns remain valid after addressing the experimental design issues, this statement is only true for the sites that the authors studied and should not be a generalized conclusion. Depending on the site slope and extent of high, mid, and low zones, a number of different outcomes could occur. For example, if the high zone is currently extremely large, this could result in an increase in the area of the lower intertidal zone with SLR.
Additional comments: I think the study is of value and, certainly, modelling of the impacts of SLR on intertidal communities needs to be further understood. However, in my opinion, there are a number of issues with the study design that I am not sure can be resolved, at least as currently described. A number of other comments not discussed above are also included in the attached document.


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: FUTURE SEA-LEVEL RISE DRIVES ROCKY INTERTIDAL HABITAT LOSS AND BENTHIC COMMUNITY CHANGE
Review round: 2
Reviewer: 1

Output:
Basic reporting: Manuscript has substantially improved since previous version.
Experimental design: The methods section is substantially easier to follow than the previous version.

Ln 263: would have also missed smaller juveniles, which presumably may be more numerous than adults.

Not necessary to answer: I wonder if the authors compared the data (Ln 239-243) with the data obtained from their previous studies to see if the cover estimates corresponded.
Validity of the findings: Data has been provided.

Results section talks mostly about the extreme upper end of the different SLR scenarios. This is fine, but de-emphasises the important finding that most of the negative impacts of SLR in the actually occur within the range of the scenarios that are far more likely to be seen within the next century.

I'd like to see a bit more clarity provided in the results. For example, the authors should refer to a figure or table when reporting a result, so the reader needn't search to find the relevant data.

Ln 327: This is a little misleading as the gooseneck barnacles were only found at one site.
Additional comments: Suggest move paragraph beginning with Line 345 to later in the discussion. It would be nicer to read about the results and how they correspond with previous studies before reading about all the caveats with the design.


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: FUTURE SEA-LEVEL RISE DRIVES ROCKY INTERTIDAL HABITAT LOSS AND BENTHIC COMMUNITY CHANGE
Review round: 2
Reviewer: 2

Output:
Basic reporting: As with the original manuscript, this was well written with appropriate literature references. The modifications made in this revision have further improved the basic reporting.
Experimental design: The authors have done an excellent job in responding to reviewer comments, I appreciate the thoroughness in explaining modifications and rebuttals. It was clear from some of their responses that a couple of my original major issues with the manuscript were due to my misunderstanding of the experimental design that edits to the manuscript have fixed (thus were not critical errors as originally thought, just methods that needed further explanation).
Validity of the findings: The study is of value and the modifications to the applicability of the results elsewhere are well done, making sure to remove some overstatements present in the first submission. In addition, some of the limitations of the study are more clearly discussed but articulated in a way that do not take away from the important findings of the study.
Additional comments: Just wanted to recognize again the excellent job of the authors in responding to the reviewer comments and critiques. After reading the first version, I had strong doubts about the value of the paper. The modifications made to the text, adjustment of some of the data analyses, and revision of the discussion have completely changed my mind. Well done. I have a very few minor edits in the included Word document.


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: ISOTOPIC BIOMONITORING OF ANTHROPIC CARBON EMISSIONS IN A MEGALOPOLIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article is written in clear and professional English. I believe that literature is sufficient to contextualize, analyze and discuss the results obtained. The structure of the article, as well as the quality of the figures is adequate.
Experimental design: I think the work is consistent with the objectives of the journal. The research questions are well defined and relevant since they propose an alternative of air quality monitoring using plants, which implies low cost of analysis. The investigation was conducted rigorously and the technical standards adequate and sufficient to lower the stated objectives. It is necessary to make some clarifications to the methodology to be completely clear, as noted below.
Validity of the findings: The article presents and validates innovative results in terms of air quality monitoring strategies. The statistical analyzes performed are adequate to support the conclusions raised by the authors, which are completely linked to the objectives, results and analyzes developed.
Additional comments: I suggest that authors comment the importance to monitor CO in particular if it represents only a fraction of the pollutants emitted into the atmosphere as the authors themselves point out.

Although the methodology used is adequate to meet the objectives set, the authors comment that they made the collection of plant material during the growth period, however it is necessary to specify that they worked with new leaves, as well as give an idea of the foliar growth rate in the species used. This is important given that the technique used for the quantification of 13C characterizes the isotopic proportion fixed during leaf formation, so it must be ensured that the growth of the leaf used was during the same period in which they average the CO concentration of their work sites. In this way, it is ensured that the calculated correlation is adequate.

Line 92. Please specify that is above sea level.
Line 93. Please specify that is elevation above sea level.


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: ISOTOPIC BIOMONITORING OF ANTHROPIC CARBON EMISSIONS IN A MEGALOPOLIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: This paper illustrates the biomonitoring of CO emissions using δ13C values in tillandsia. In my opinion, the article has too many significant issues, that can not be easily fixed, even with an extensive revision of the manuscript.
The abstract sounds a bit confused: for example, there is no need to specify here some statistical details about the significance of the tests or other methodological parameters. On the other hand, the aim of the paper must be stated much more clearly than it is now.
I am puzzled about the choice of the pollution marker made in this paper. Although fuel combustion indeed generates CO and CO2, but also many other gaseous and non-gaseous compounds and/or elements that can be much more easily linked to the emission. The authors report some of them in the methods (e.g. line 103: O3, NOx, NO2, NO, PM10 PM2.5).
As the authors state, the amounts of emitted CO from combustion is "very low or insignificant" if compared to CO2 emission. That makes the use of this marker quite problematic.
The aim of the paper is not clearly stated. Also, some crucial aspects of the method used are not enough introduced. A general audience may not be familiar with the relationship occurring between CO emissions and δ13C values accumulated in the plant.
There are also some conceptual misunderstanding of biomonitoring techniques (e.g. line 71: in fact, they are a complementary approach to air quality monitoring and do not substitute chemical-physical procedures. They give additional, biological information on the response to the pollution that can not be retrieved from chemical data by themselves.
I also see major problems in the sampling design. I acknowledge that the distribution of tillandsia is not regular. Still, there are dozen of sampling designs that can face this issue and save the probabilistic base of the location of sampling points. Even though a preferential sampling may be an option in some cases, it generates critic issues when data are used for making inference on non-sampled locations in the study area (e.g. mapping through interpolation), as in the case of this paper.
These problems become more and more critical when trying to put in correlation δ13C values and interpolated CO values with an unknown error.
Moreover, the discussion is in some parts too much speculative and not always related to the results presented in the study (e.g. 222-227).
Experimental design: Major issues both in the sampling design and in the definition of the statistical model.
Validity of the findings: Although there is some useful perspective, the issues described above make it difficult to come to robust conclusions.
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: ISOTOPIC BIOMONITORING OF ANTHROPIC CARBON EMISSIONS IN A MEGALOPOLIS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript evaluate changes in “Tissue carbon content and the δ13C values for the epiphytic CAM bromeliad Tillandsia recurvata and the relationship of both parameters with the CO concentrations in the Valley of Mexico basin”. This research is novel and the topic fits well to the scope of the journal, because it is the first studie to investigating relationship between carbon emissions and the plant´s isotopic composition. However, my main concern about this manuscript is statistycal analysis related with desing. I think that land use types (urban parks, agricultural and natural protected areas), should be included as explanatory factor in regression models. Thus, I suggest to explicate how many sites (22 sites in total) were  distributed within of urban parks, agricultural and natural protected areas in this study??. In addition, I suggest to include CO concetrations and land use types as explicator factors in the new  multiple regresion model (normal distribution) or Generalized linear model (not normal distribution).

References

Please the authors should include all references following authors guide of journal

Correct format

Sala OE, Chapin III SF, Armesto JJ, Berlow E, Bloomfield J, Dirzo R, Huber-Sanwald E, Huenneke LF, Jackson RB, Kinzig A, Leemans R, Lodge DM, Mooney HA, Oesterheld M, Poff NL, Sykes MT, Walker BH, Walker M, Wal DH (2000) Global biodiversity scenarios for the year 2100. Science 344 287:1770–1774. doi: 10.1126/science.287.5459.1770.

Incorrrect format

Silva, S. J., Arellano, A. F., & Worden, H. M. (2013). Toward anthropogenic combustion emission constraints from space-based analysis of urban CO2 /CO sensitivity. Geophysical Research 349 Letters, 40(18), 4971–4976. doi:10.1002/grl.50954
Experimental design: The manuscript evaluate changes in “Tissue carbon content and the δ13C values for the epiphytic CAM bromeliad Tillandsia recurvata and the relationship of both parameters with the CO concentrations in the Valley of Mexico basin”. This research is novel and the topic fits well to the scope of the journal, because it is the first studie to investigating relationship between carbon emissions and the plant´s isotopic composition. However, my main concern about this manuscript is statistycal analysis related with desing. I think that land use types (urban parks, agricultural and natural protected areas), should be included as explanatory factor in regression models. Thus, I suggest to explicate how many sites (22 sites in total) were  distributed within of urban parks, agricultural and natural protected areas in this study??. In addition, I suggest to include CO concetrations and land use types as explicator factors in the new  multiple regresion model (normal distribution) or Generalized linear model (not normal distribution).

2. Materials and Methods
Line 90: Study region
I suggest to explicate how many sites (22 sites in total) were distributed within of urban parks, agricultural and natural protected areas in this study.
Line 100 and 109: Atmospheric CO concentration and Biomonitoring

I suggest to join the following subtitles, for instance:

Atmospheric CO concentration and Biomonitoring
Geoestatitical and Statistical analysis

Line 131-138: Linear regressions were calculated to determine the relationship between CO concentrations and carbon content (% dry weight), as well as the isotopic composition (δ13C values) for Tillandsia recurvata in the Valley of Mexico. The differences between sites for the carbon content and the δ13C values were determined by means of the Kruskal-Wallis one-way analysis of variance by ranks, followed by a Nemenyi´s post-hoc tests for pairwise multiple comparisons (p ≤ 0.05). The analyses were conducted using the Pairwise multiple comparison of mean ranks package (PMCMR) in R (version 3.5.3, R Core Team, R foundation for Statistical Computing, Vienna, Austria; Pohlert, 2014).

In my opinion, the tissue carbon content and the δ13C values for the epiphytic CAM bromeliad Tillandsia recurvata and the relationship of both parameters with the CO concentrations and land use types can be analyzed by multiple regresion model (normal distribution) or Generalized linear model (not normal distribution), and post-hoc Tukey test.

3. Results and Discsussion.

In my opinion,these sections should be rewritten with results the new statistycal analysis.
Validity of the findings: 2. Materials and Methods
Line 90: Study region
I suggest to explicate how many sites (22 sites in total) were distributed within of urban parks, agricultural and natural protected areas in this study.
Line 100 and 109: Atmospheric CO concentration and Biomonitoring

I suggest to join the following subtitles, for instance:

Atmospheric CO concentration and Biomonitoring
Geoestatitical and Statistical analysis

Line 131-138: Linear regressions were calculated to determine the relationship between CO concentrations and carbon content (% dry weight), as well as the isotopic composition (δ13C values) for Tillandsia recurvata in the Valley of Mexico. The differences between sites for the carbon content and the δ13C values were determined by means of the Kruskal-Wallis one-way analysis of variance by ranks, followed by a Nemenyi´s post-hoc tests for pairwise multiple comparisons (p ≤ 0.05). The analyses were conducted using the Pairwise multiple comparison of mean ranks package (PMCMR) in R (version 3.5.3, R Core Team, R foundation for Statistical Computing, Vienna, Austria; Pohlert, 2014).

In my opinion, the tissue carbon content and the δ13C values for the epiphytic CAM bromeliad Tillandsia recurvata and the relationship of both parameters with the CO concentrations and land use types can be analyzed by multiple regresion model (normal distribution) or Generalized linear model (not normal distribution), and post-hoc Tukey test.

3. Results and Discsussion.

In my opinion,these sections should be rewritten with results the new statistycal analysis.

4. Conslusions

Line 334: pollutants such as NOx, SO2, O3, heavy metals, particulate matter, etc

In my opinion, authors should deleted the follow word “etc.”
Additional comments: PeerJ-41903

Dear Editor,

The manuscript evaluate changes in “Tissue carbon content and the δ13C values for the epiphytic CAM bromeliad Tillandsia recurvata and the relationship of both parameters with the CO concentrations in the Valley of Mexico basin”. This research is novel and the topic fits well to the scope of the journal, because it is the first studie to investigating relationship between carbon emissions and the plant´s isotopic composition. However, my main concern about this manuscript is statistycal analysis related with desing. I think that land use types (urban parks, agricultural and natural protected areas), should be included as explanatory factor in regression models. Thus, I suggest to explicate how many sites (22 sites in total) were  distributed within of urban parks, agricultural and natural protected areas in this study??. In addition, I suggest to include CO concetrations and land use types as explicator factors in the new  multiple regresion model (normal distribution) or Generalized linear model (not normal distribution).
__________________________________________________________________________
Further comments:
1. Introduction
Line 37: Atmospheric pollution has become a serious threat for human health and the environment.

Here, authors should add reference
Line 39-41: For example, Mexico City, with vertiginous growth of industrial and household activities, as well as numerous motor vehicles of all classes, has seen an increase of emissions of different pollutants to the atmosphere.
Here, authors should add reference

Line 47-51: The combustion of carbonaceous fuels generates two main carbon products, carbon monoxide and carbon dioxide. However, the proportion in which they are emitted can vary. For example, when a motor works in optimal conditions, that is when the mixture of air, fuel, and temperature inside an automobile engine is ideal, the complete combustion of the fuel is achieved (high efficiency), resulting in the complete oxidation of carbon and subsequent emission of CO2.

Here, authors should add reference

Line 80-81: Although, the carbon isotopic composition of this plant has been
reported for polluted and non-polluted sites

Here, authors should add reference

2. Materials and Methods
Line 90: Study region
I suggest to explicate how many sites (22 sites in total) were distributed within of urban parks, agricultural and natural protected areas in this study.
Line 100 and 109: Atmospheric CO concentration and Biomonitoring

I suggest to join the following subtitles, for instance:

Atmospheric CO concentration and Biomonitoring
Geoestatitical and Statistical analysis

Line 131-138: Linear regressions were calculated to determine the relationship between CO concentrations and carbon content (% dry weight), as well as the isotopic composition (δ13C values) for Tillandsia recurvata in the Valley of Mexico. The differences between sites for the carbon content and the δ13C values were determined by means of the Kruskal-Wallis one-way analysis of variance by ranks, followed by a Nemenyi´s post-hoc tests for pairwise multiple comparisons (p ≤ 0.05). The analyses were conducted using the Pairwise multiple comparison of mean ranks package (PMCMR) in R (version 3.5.3, R Core Team, R foundation for Statistical Computing, Vienna, Austria; Pohlert, 2014).

In my opinion, the tissue carbon content and the δ13C values for the epiphytic CAM bromeliad Tillandsia recurvata and the relationship of both parameters with the CO concentrations and land use types can be analyzed by multiple regresion model (normal distribution) or Generalized linear model (not normal distribution), and post-hoc Tukey test.

3. Results and Discsussion.

In my opinion,these sections should be rewritten with results the new statistycal analysis.

4. Conslusions

Line 334: pollutants such as NOx, SO2, O3, heavy metals, particulate matter, etc

In my opinion, authors should deleted the follow word “etc.”

5. References

Please the authors should include all references following authors guide of journal

Correct format

Sala OE, Chapin III SF, Armesto JJ, Berlow E, Bloomfield J, Dirzo R, Huber-Sanwald E, Huenneke LF, Jackson RB, Kinzig A, Leemans R, Lodge DM, Mooney HA, Oesterheld M, Poff NL, Sykes MT, Walker BH, Walker M, Wal DH (2000) Global biodiversity scenarios for the year 2100. Science 344 287:1770–1774. doi: 10.1126/science.287.5459.1770.

Incorrrect format

Silva, S. J., Arellano, A. F., & Worden, H. M. (2013). Toward anthropogenic combustion emission constraints from space-based analysis of urban CO2 /CO sensitivity. Geophysical Research 349 Letters, 40(18), 4971–4976. doi:10.1002/grl.50954

Sincerely,

PhD. Angel Raimundo Benitez Chavez.
Departamento de Ciencias Biológicas.
Sección de Ecología y Sistemática
Herbario HUTPL
Universidad Técnica Particular de Loja
Telf: 072570275 Ext: 3034, Celular: 0985182195
San Cayetano Alto. Campus Universitario. Loja-Ecuador