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: INTER- AND INTRASPECIFIC VARIATION IN THE ARTIBEUS SPECIES COMPLEX DEMONSTRATES SIZE AND SHAPE PARTITIONING AMONG SPECIES
Review round: 1
Reviewer: 4

Output:
Basic reporting: The manuscript is well written and follows the PeerJ standards in terms of structure. Figures are generally well labeled and illustrate the results correctly. Some graphical elements are lacking, specifically the representation of shape deformations grids on figures 4 (PC2), 5 (CAC), and 6 (PC1 and 2). Tables 1 and 2 legends lack some relevant elements to properly understand them, namely the statistical terms (Df, SS, MS, etc.). Data provided in the supplementary material is enough to replicate figures and is easily accessible and adequately explained. In terms of general structure, the manuscript seems adequate.
Experimental design: The introduction adequately highlights the paper's conceptual background and identifies the gap in the knowledge that the paper expects to fill. Specifically, the paper seeks to perform an exploratory analysis of the inter and intraspecific shape variation in the Artibeus species complex, a genus known for its conserved morphology. Sample sizes are more than adequate for the proposed investigation. The methodology is designed to investigate if species differ and if different populations of a more widely distributed species also differ. The methods used are straightforward and rely on linear models to examine these issues and the potential presence of sexual dimorphism and allometry. Methods are satisfactorily explained in most cases, and results are transparently presented and discussed.

Findings from this manuscript stem directly from the investigation of the available dataset. The result that Artibeus species are more different than previously imagined is new and exciting and points to the possibility of local adaptation and niche partition. The evaluation of the intraspecific dataset shows that local adaptation is also a possibility in A. lituratus. Sexual dimorphism also suggests that ecological differences between males and females of the group might express in terms of sexual dimorphism.
Nevertheless, the paper neglect some aspects of this morphological diversity. For example, besides broad stroke differences described on the PC1 for both views and some aspects of sexual dimorphism, little is known how species diverge. Descriptions of PC2 are not given, nor shape deformations associated with CAC. This absence is even more problematic as PC1 and the allometric vector seems to share some common variation. Results show that species differ after accounting for differences in size, but we cannot say precisely how. This problem can be solved by amending the current methodology (correctly describing and showing differences between species and sexes) or using new methods (see comments to the author).
Validity of the findings: Results from the analysis are adequately explained, and the analyses corroborate the conclusions. The results are new and can be interesting for anyone interested in either taxonomy, ecology, or evolution of the group. The only issue with the conclusions is the supposed lack of clinal variation in the intraspecific dataset. While I agree that there is no perfect geographical pattern, it is not possible to discard the existence of clinal variation without explicitly investigating it (see comments to the author). While broad patterns of shape variation might not be geographically determined, smaller scale-variation might be geographically structured. A proper examination of geographical variation might help to solve this issue. Furthermore, I feel that other aspects of the methodology and discussion can be improved to support the conclusions better and improve readability (see comments to the author).
Additional comments: I found the paper reasonably well designed, and the methodology is good enough to justify the discussion. However, the paper touches on a couple of topics that can be better explored with available methods that put the discussion on a sounder footing. In that regard, anything that I suggest below in terms of methodology should be viewed as ways to improve the paper and do not reflect any flaws of the paper. I will list topics and what methods can be used to improve the results and conclusions.

Data processing- The author employs the standard method of evaluating each view independently, which entails that all methods have to be replicated twice. However, some recent papers have suggested ways to assess different views/configurations on the same dataset (Antonio et al. 2019. Seeing the wood through the trees. Combining shape information from different landmark configurations. Hystrix-the Italian Journal of Mammalogy, 30(2), 157–165. http://doi.org/10.4404/hystrix–00206-2019; Collyer et al. 2020. Making Heads or Tails of Combined Landmark Configurations in Geometric Morphometric Data. Evolutionary Biology 47, 193–205. http://doi.org/10.1007/s11692-020-09503-z). The author should contemplate using this methodology for two reasons. One, it might improve readability by simplifying methods, results, and discussion. Two, by analyzing the skull shape as a whole, different patterns might arise. I suggest using the methodology exposed in Antonio et al. (2019) as a starting point (but keeping in mind comments made by Collyer et al. 2020). Furthermore, regarding semi-landmark sampling on the zygomatic on the ventral view: the number of points seems excessive. The same variation can probably be sampled with fewer points (even half of the points used).

Niche partitioning- Most of the justification for the argument that niche partitioning might be guiding differences in species relies on the fact that species were significantly different on the non-parametric MANOVA tests. However, MANOVAs tests for the differences in average, not overlap between groups, which would be more descriptive of ecomorphological niche partition. To directly evaluate morphospace overlap, the author can employ two different but similar methodologies. One is to use Linear Discriminant Analysis to calculate between species reclassification rates as a measure of overlap (e.g., Machado, F. A., & Teta, P. 2020. Morphometric analysis of skull shape reveals unprecedented diversity of African Canidae. Journal of Mammalogy, 26, 32–12. http://doi.org/10.1093/jmammal/gyz214). Since LDAs require matrix inversion, a dimensionality reduction is always advised before using this method (see Miranda et al. 2017. Taxonomic review of the genus Cyclopes Gray, 1821 (Xenarthra: Pilosa), with the revalidation and description of new species. Zoological Journal of the Linnean Society, 183(3), 687–721.http://doi.org/10.1093/zoolinnean/zlx079). One alternative is to use the package nicheROVER (Swanson et al. 2015. A new probabilistic method for quantifying n‐dimensional ecological niches and niche overlap. Ecology 96.2: 318-324.), which do not require matrix inversion nor equality between covariance matrices between groups, but still uses multivariate normal distributions to model populations. If that assumption is not reasonable, one alternative is "hypervolume" (Blonder et al. 2014. "The n‐dimensional hypervolume." Global Ecology and Biogeography 23.5: 595-609.), which allows for the calculation of more complex hypervolumes and overlaps.

Phylogenetic signal and evolutionary patterns- A high phylogenetic signal by itself can be consistent with both neutral evolution (Brownian motion) and early burst scenarios. The author might consider employing a Diversity Through Time to supplement their phylogenetic signal analysis (Murrell, D. J. (2018). A global envelope test to detect non-random bursts of trait evolution. Methods in Ecology and Evolution, 9(7), 1739–1748. http://doi.org/10.1111/2041-210X.13006). DTT might give some insight into the process leading to the diversification of a given phenotype (e.g., Segura et al. 2020. Integration or Modularity in the Mandible of Canids (Carnivora: Canidae): a Geometric Morphometric Approach, 1–13. http://doi.org/10.1007/s10914-020-09502-z). Stable patterns of disparity are consistent with stability, while quick drops of disparity over time are associated with bursts of diversification. This might help to better discuss evolutionary scenarios that might have shaped the diversification of the group.

Geographical variation- One possibility to evaluate geographical patterning in the intraspecific dataset is through the use of linear models with geographical variables. This can be done in two main ways: trend surface analysis, which is a regression of geographical coordinate derived variables on shape, and eigenvector mapping, that decomposes spatial structure in new eigenvectors that represent geographical variation in multiple scales. See Cardini et al. (2010. Biogeographic Analysis Using Geometric Morphometrics: Clines in Skull Size and Shape in a Widespread African Arboreal Monkey. In A. M. T. Elewa (Ed.), Morphometrics for Nonmorphometricians (5 ed., Vol. 124, pp. 191–217). Berlin, Heidelberg: Springer Berlin Heidelberg. http://doi.org/10.1007/978-3-540-95853-6_8) and references therein. Another more straightforward and less powerful alternative is employing a Mantel test on Procrustes distance and geographical distances. The absence of a signal on any of these analyses will support the conclusion that there is little or no geographical structure on the data.

Still, regarding intraspecific variation, one question that is not explored is how similar it is to the interspecific variation in magnitude and pattern. Magnitude could be investigated by calculating disparity for both intraspecific and interspecific datasets using the function morphol.disparity() from the geomorph package. To examine if intra and interspecific variation patterns coincide, the author can evaluate the concordance between the leading PC of intraspecific data and the PC of a phylogenetic covariance matrix (see Segura et al. 2020; Revell, 2009. Size-Correction and Principal Components for Interspecific Comparative Studies. Evolution, 63(12), 3258–3268. http://doi.org/10.1111/j.1558-5646.2009.00804.x; Slater and Friska .2019; Hierarchy in adaptive radiation: A case study using the Carnivora (Mammalia). Evolution, 73(3), 524–539. http://doi.org/10.1111/evo.13689; Parsons et al. 2020. Skull morphology diverges between urban and rural populations of red foxes mirroring patterns of domestication and macroevolution. Proceedings of the Royal Society of London. Series B, Biological Sciences, 287(1928), 20200763–10. http://doi.org/10.1098/rspb.2020.0763). A simple vector correlation or angle comparison could be enough to direct discussion in this regard. This could help to evaluate if geographical variation within-species follows the same pattern that between species evolution, suggesting common ecological drivers of both levels of morphological adaptation (see Schiaffini et al. 2019. Geographic variation in skull shape and size of the Pampas fox Lycalopex gymnocercus (Carnivora: Canidae) in Argentina. Mammalian Biology - Zeitschrift Fur Saugetierkunde, 97, 50–58. http://doi.org/10.1016/j.mambio.2019.04.001). Vector correlation might also be interesting to evaluate if patterns of divergence (PC1) and allometric patterns coincide (e.g., Machado and Teta, 2020). Vector correlation and angle comparisons can be implemented with the function angleTest() from the package Morpho.

Minor comments

L74- This is a strong paragraph to introduce your model system. Consider starting the paper with this one instead.
L95- Rossoni et al. (2019) is not a geometric morphometric investigation.
L174-177- A phylogenetic ANOVA wouldn't be appropriate for an investigation into between-species differences. This phrase is not necessary.
L186-189- Why not simply call "countries" "populations" and name them according to countries? Also, the investigation of "within country variation" makes little sense, as countries are arbitrary geographical categories. You don't need to justify why you have two Mexican samples.
L257-258- It is not clear from the text if this passage refers to the analysis of shape or size. If the author refers to shape here, then the interaction between those factors does not mean what is stated. Instead, it means that allometric relations change with species and with each sex within each species. If this passage refers to size, it needs to be rephrased to better express that.
L308- It is unclear if this sample is adequate to identify differences between Atlantic Forest and the Amazon. Samples seem to be marginal to these biomes, so this statement appears unnecessary.


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: INTER- AND INTRASPECIFIC VARIATION IN THE ARTIBEUS SPECIES COMPLEX DEMONSTRATES SIZE AND SHAPE PARTITIONING AMONG SPECIES
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Author was very responsive to my and other reviewer comments. All previous concerns and comments have been addressed in this revised manuscript.


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

Input:
Title: INTER- AND INTRASPECIFIC VARIATION IN THE ARTIBEUS SPECIES COMPLEX DEMONSTRATES SIZE AND SHAPE PARTITIONING AMONG SPECIES
Review round: 2
Reviewer: 2

Output:
Basic reporting: Greetings,

I have reviewed Dr. Hedrick’s manuscript, which presents a study of the variation in skull shape within and among Artibeus species. Additionally, I have looked at the review files that were part of the submission. The reviewers’ comments from the first round of reviews were extensive and thorough and I largely agree with the points they made, and the author seems to have addressed them appropriately in this version. As a result, I only have suggestions that involve text edits to further improve the manuscript.

Abstract:
L19-20: This sentence needs work. The fact that species coexist means that they have not competitively excluded one another and therefore there is niche partitioning. This can be achieved through differences in non-morphological traits (e.g., size, behavior, acoustics). What the dearth of variation may mean is that skull shape changes may have not evolved as a result of competition.
L25: replace “niches” with “ecological resources”

Introduction:
L68-69: All species live in sympatry with related species.
L25: also vertebrates.
L95-105: this paragraph could be greatly condensed. Geometrics morphometrics is now over 30 years old, so presenting it as a revolutionary tool seems outdated and unnecessary. I recommend deleting this text starting with "Caliper-based linear morphometrics..."
L111-113: this does require further explanation; why would geometric morphometrics actually allow to capture these differences? It is because it allows to disentangle shape from size variation?
L117: delete “rather than linear morphometrics”
L117: how many species are there in the Artibeus spp. complex? Clarify what portion of the variation is examined here.
L119-120: “which may suggest differences in niche partitioning” should be balanced with a non-adaptive explanation (e.g., “or non-adaptive processes such as drift”). In general, the manuscript strikes me as very adaptationist – not all morphological differences are due to adaptation, as some of the results illustrate.
L122: what is the prediction and justification for examining sexual dimorphism? This should be added.
L128: add justification why this species was selected for the intraspecific study.
L132: underlying causes are discussed, not assessed.

Methods:
L163-165: clarify here and in figure legend -- were the semilandmarks placed evenly spaced along the curve? Add them to the curves in Fig. 2.
L194: means of what?
L196: clarify this is Kmult.
L220: add text to clarify why country was used as a proxy for locality, since this is unusual.
L224: the use of “population” here seems problematic. Replace with “individuals in portions of the geographic range (countries)…”

Results:
L315-318: this could favor non-adaptive hypotheses – a strong phylogenetic signal in size differences and thereby shape via allometry.
L341-342: it’s unclear how these tests were conducted and what is being shown in the table (what are the coefficients shown?). Clarify in methods and Table legend.

Fig 4: change large Artibeus symbols to triangles for readability and consistency.

Discussion:
The discussion section largely recapitulates the results, and is still narrowly focused on phyllostomid bats. For a journal like PeerJ, the results should be discussed in the context of the broader literature on morphological variation, sexual dimorphisms, etc.
L360: replace “successful” with “diverse”.
L381: one possible explanation, if these differences result in performance differences, resource use, etc.
L392: replace “workers” with “studies”.
L416-417: this sentence is very vague; state what you mean more specifically.
L418-419: this sentence suggests that plasticity selects on morphology, but the studies cited do not demonstrate this.
L420-422: this reference is not in the reference list. Did this study actually couple quantitative dietary data with behavioral data and modeling of morphological evolution (or paleontological studies) to demonstrate this?
L433-436: this is assuming the variation leads to functional consequences of importance to access food resources - size may simply override these though.
L444: or other factors that affect body size may “drag” the evolution of skull size and shape with it.
L455-456: unclear what is meant here by “the way size is calculated”
L478-479: how about defense, fighting other males, tent making?
L512-513: there is a rich literature on this for mammals and other vertebrates, expand the scope beyond this narrow group.
L568-569: what is the purpose of this sentence?
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: Greetings,

I have reviewed Dr. Hedrick’s manuscript, which presents a study of the variation in skull shape within and among Artibeus species. Additionally, I have looked at the review files that were part of the submission. The reviewers’ comments from the first round of reviews were extensive and thorough and I largely agree with the points they made, and the author seems to have addressed them appropriately in this version. As a result, I only have suggestions that involve text edits to further improve the manuscript.

Abstract:
L19-20: This sentence needs work. The fact that species coexist means that they have not competitively excluded one another and therefore there is niche partitioning. This can be achieved through differences in non-morphological traits (e.g., size, behavior, acoustics). What the dearth of variation may mean is that skull shape changes may have not evolved as a result of competition.
L25: replace “niches” with “ecological resources”

Introduction:
L68-69: All species live in sympatry with related species.
L25: also vertebrates.
L95-105: this paragraph could be greatly condensed. Geometrics morphometrics is now over 30 years old, so presenting it as a revolutionary tool seems outdated and unnecessary. I recommend deleting this text starting with "Caliper-based linear morphometrics..."
L111-113: this does require further explanation; why would geometric morphometrics actually allow to capture these differences? It is because it allows to disentangle shape from size variation?
L117: delete “rather than linear morphometrics”
L117: how many species are there in the Artibeus spp. complex? Clarify what portion of the variation is examined here.
L119-120: “which may suggest differences in niche partitioning” should be balanced with a non-adaptive explanation (e.g., “or non-adaptive processes such as drift”). In general, the manuscript strikes me as very adaptationist – not all morphological differences are due to adaptation, as some of the results illustrate.
L122: what is the prediction and justification for examining sexual dimorphism? This should be added.
L128: add justification why this species was selected for the intraspecific study.
L132: underlying causes are discussed, not assessed.

Methods:
L163-165: clarify here and in figure legend -- were the semilandmarks placed evenly spaced along the curve? Add them to the curves in Fig. 2.
L194: means of what?
L196: clarify this is Kmult.
L220: add text to clarify why country was used as a proxy for locality, since this is unusual.
L224: the use of “population” here seems problematic. Replace with “individuals in portions of the geographic range (countries)…”

Results:
L315-318: this could favor non-adaptive hypotheses – a strong phylogenetic signal in size differences and thereby shape via allometry.
L341-342: it’s unclear how these tests were conducted and what is being shown in the table (what are the coefficients shown?). Clarify in methods and Table legend.

Fig 4: change large Artibeus symbols to triangles for readability and consistency.

Discussion:
The discussion section largely recapitulates the results, and is still narrowly focused on phyllostomid bats. For a journal like PeerJ, the results should be discussed in the context of the broader literature on morphological variation, sexual dimorphisms, etc.
L360: replace “successful” with “diverse”.
L381: one possible explanation, if these differences result in performance differences, resource use, etc.
L392: replace “workers” with “studies”.
L416-417: this sentence is very vague; state what you mean more specifically.
L418-419: this sentence suggests that plasticity selects on morphology, but the studies cited do not demonstrate this.
L420-422: this reference is not in the reference list. Did this study actually couple quantitative dietary data with behavioral data and modeling of morphological evolution (or paleontological studies) to demonstrate this?
L433-436: this is assuming the variation leads to functional consequences of importance to access food resources - size may simply override these though.
L444: or other factors that affect body size may “drag” the evolution of skull size and shape with it.
L455-456: unclear what is meant here by “the way size is calculated”
L478-479: how about defense, fighting other males, tent making?
L512-513: there is a rich literature on this for mammals and other vertebrates, expand the scope beyond this narrow group.
L568-569: what is the purpose of this sentence?


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: ERPRED: A WEB SERVER FOR THE PREDICTION OF SUBTYPE-SPECIFIC ESTROGEN RECEPTOR ANTAGONISTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: In Keywords: QSAR is quantitative structure-activity relationship. No need to have both.

When the abbreviated names appear in the manuscript at the first time, the full names should be shown and the abbreviated comes after in parentheses. Line 30: MCC; Line 97: LDB. Full names should be shown here.

There are numerous grammar and language issues, which need to be addressed. For example: lines 19-20, 108-110, 159, 355, etc. Several long sentences are confusing and need to be simplified and rephrased, eg. Lines 101-104, 242-246.

Line 120, “8” should be deleted.

Line 134-135, format is wrong for the citation.

Line 214, should be Matthews correlation coefficient not Matthew’s correlation coefficient.
Experimental design: ERs are nuclear receptors, so their ligands usually are classified as agonists and antagonists. Inhibitors are for enzymes. To use antagonists rather than inhibitors in this manuscript is more scientifically sound.

As we all know, the quality of dataset is crucial for the QSAR modeling. We need to know more details about the data sources and information. The manuscript should explain what assays were performed to get IC50s in the original articles. In vitro binding and functional assays could give very different results, sometime more than 1 log unit, which will affect the classification of actives (pIC50 >=6) and inactives (pIC50>=5).  Also, how the ligands were prepared before calculations of descriptors is not clear in the current manuscript. Details should be provided in Experimental Section, (eg, protonation, inclusion of racemic compounds, etc.) because different descriptors will be obtained for different ligand preparations. In addition, it is good to show what the structural diversity of the dataset is.

The authors used the Kennard Stone sampling method; however, the iterative random sampling method is more commonly used and generates more reliable results. Authors should try iterative random sampling and compare with Kennard Stone method to see how different the results are.

The current discussion in “Structural interpretation of differences in binding sites” section is irrelevant to the main topic of this manuscript. As the authored mentioned, the LBDs of ERα and ERβ share 55% sequence identity. Antagonists for both receptors should have cross binding affinity for the other receptor, and structurally may contain similar features for binding potency and different features for specificity, as QSAR studies show. In this section, authors are recommended to discuss how the similar and different features bind to the receptors and contribute to the potency and specificity structurally.

In the Chemical space analysis section, ALogP and MW were shown to be significant different between actives and inactives for ER-alpha. The means for both properties are not clear, and should be stated in the texts.

In line 110-113, it described what happens after binding to agonists to ERs. Since this manuscript focuses on antagonists, authors should add the description here about what will happen after antagonists’ binding to the receptor.

What is the percentage of actives and inactive in the internal and external dataset for both ER receptors? They may impact the performance of the QSAR models.

Line 368-369, PubChemFP777 is not 4-methylphenol, but hydrogenated one, the description about 4-methylphenol is irrelevant to the discussion

Line: 494-497: “Thus, this study aimed to qualitatively and quantitatively address these issues by building a QSAR model that would distinguish active compounds from inactive compounds for ERα and ERβ while also predicting the binding affinity for active compounds towards either ER subtype”. The current QSAR models are for classification of actives and inactives only. How can they predict binding affinity for actives?
Validity of the findings: no comment
Additional comments: This manuscript “ERpred: A web server for the prediction of estrogen receptor subtype-specific bioactive inhibitors” described the development of classification QSAR models for estrogen receptor (ER) antagonists by extracting ligands from the ChEMBL database and then a publicly available web server (ERpred) based on the models. ER is a member of the nuclear receptor family and consists of two main subtypes (ERα and ERβ), which have been shown to paly different roles in the development and metastasis of breast cancer.  The development of compounds possessing ER subtype specificity still represents unmet medical need and warrants further studies. Publication of this manuscript will add values to the scientific community.


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: ERPRED: A WEB SERVER FOR THE PREDICTION OF SUBTYPE-SPECIFIC ESTROGEN RECEPTOR ANTAGONISTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript of Schaduangrat and coworkers (#52348) introduces ERpred, a web server tailored for the prediction of inhibitors for the two estrogen receptor (ER) proteins alpha and beta, two well known pharmacological targets for breast cancer. By performing a classification structure-activity relationship (CSAR) of known inhibitors from the ChEMBL database, a set of structural features important for the compound activity was determined by using a random forest algorithm, which is a commonly used classification method. A number of molecular characteristics (e.g., presence of aromatic rings, or other functional groups) were identified, which are used in the web server to predict bioactivity of novel compounds towards the protein targets.

This work is interesting and, as far as I can see, well conducted. The results do not seem to be entirely outstanding, but predicting the existence of active and selective molecules for two proteins simultaneously is admittedly not an easy task. The ERpred web server could serve the scientific community by providing predictions that can help to filter out compounds in the pipeline of the selection of novel ER-targeting compounds. The manuscript is also generally well written, with a few minor mistakes (some of them will be pointed out below). Figures and tables are also clear and informative.

Some suggestions:

Line 20, “Estrogen receptor alpha and beta [...] represents the fundamental and critical determinants of clinical outcomes”. This part is not clear and should be changed. What is it supposed to be critical (their existence, abundance, or...)? To me, they are just pharmacological protein targets.

Line 29, “Ac of 94.65% 30 and 92.25% and MCC of 0.89 and 0.76 for ERa and ERß, respectively”. These quantities are not defined yet, and it seems also strange that they are not expressed with the same notation (0.89 = 89%).

Line 44: “Thailand, breast cancer ranks third behind lung and liver cancers accounting for an estimated 11.4% of new cases and 114,199 deaths in 2018 (International Agency for Research on Cancer, 2019)”. This is relevant for the Authors and their compatriots, but much less in the international context of the wide readership of this journal.

Line 54: “desperately needed”. I would use a less alarming adverb.

Line 56: “Estrogen receptors (ER) is a...”. Please correct this part.

Line 69: “more prominent role on the mammary gland and uterus”. Which type of role?

Line 83: “the effectiveness of this drug”. It is not entirely clear which compound is being referred to, and I would suggest to name it explicitly.

 Line 134: “Estrogen receptor binding affinity estimated by QSAR”. This is cited as a reference, but citation is not clear.

Line 158: “molecular descriptors are important for QSAR studies as it characterize”. Please correct this part.

Line 169: “constant and near constant variables”. What do these quantities represent?

Line 206: “The mean decrease of the Gini index (MDGI) was utilized to estimate the important descriptors”. Maybe using a reference already here would be useful.

Line 212: “True positives (TP), true negatives (TN), false positives (FP) and false negatives (FN)”. Please correct or delete this sentence.

Line 219, Equation 2. What is the “=” intended for?

Line 233: “PCA bounding box”. This part is not clear. Please also note that, although it is pretty clear what PCA refers to, this acronym was never defined (and here it is used for the first time).

Line 269: “number of hydrogen bond donors (> 5)”. This should be “< 5”.

Line 282: “were observed to be less than those”. Maybe “lower”?

Line 379: “(Bisphenol S) (National Center for Biotechnology Information, 2020)”. This reference should be adequately explained, e.g. “as described in the report on...”.

Line 432: “water bridge for Arg394/346” (and similarly line 446, “water molecule...”). It is not entirely obvious to me what this refers to. Is it a crystallographic water bridging two Arg residues? Can a reference be given?

Line 436: “ERbeta possesses an additional binding (Leu476)”. Maybe “binder”? In any case, this expression is confusing.

Line 449: “appear to be commensurate between the two ERs”. The term “commensurate” is not clear.

Line 470: “the bioactivity for 2 classes of proteins (herein ERa and ERß)”. Why not simply “for two proteins”?

Line 501: “afforded the best performance while also affording...”. This part is not very elegant.

Line 499. “Looking forward, molecular dynamic simulations could play a role in analysis of ER subtype specificity which should be explored in future work”. This conclusion is really puzzling to me. It does not have anything to do with this work, and it is not clear how molecular dynamics (please note the ending “s” in “dynamics”) will be interesting as a continuation of this work. The sentence could be removed.
Experimental design: No comment.
Validity of the findings: No comment.
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: ERPRED: A WEB SERVER FOR THE PREDICTION OF SUBTYPE-SPECIFIC ESTROGEN RECEPTOR ANTAGONISTS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The authors have investigated a large-scale classification structure-activity relationship (CSAR) study of inhibitors from the ChEMBL database, which consisted of an initial set of 11,618 compounds. They are deployed as the publicly available web server called ERpred at http://codes.bio/erpred.
I have read the manuscript and put my comments wherever is needed. The manuscript is clearly written in professional, unambiguous language. However, the part of predicting the binding affinity for active compounds is not clear therefore more information for this part is needed.
The idea of the work is relevant and interesting and the article is publishable after making the following minor corrections:
Experimental design: 'no comment'
Validity of the findings: 'no comment'
Additional comments: 1.	Put the full name of ligand binding domains at lines 97.

2.     Many references cited In Lines 133- 137: (Anstead, Carlson & Katzenellenbogen, 1997; Serafimova et al., 2007; Xiang et al., 2009; Toropov et al., 2012; Chang et al., 2013; “Estrogen receptor binding affinity estimated by QSAR,” 2015; Ribay et al., 2016; Suvannang et al., 2017, 2018; Lee & Barron, 2017; Pavlin et al., 2018; Pang et al., 2018; Balabin & Judson, 2018; Cotterill et al., 2019; Bafna et al., 2020). You must put the references in order of years and correct this reference “Estrogen receptor binding affinity estimated by QSAR,” 2015 (write it in the same style).

3.     At line 302 put the full name of  OECD

4.	Step 2 is not quite clear (line 479- 481). Please explain this step


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: ERPRED: A WEB SERVER FOR THE PREDICTION OF SUBTYPE-SPECIFIC ESTROGEN RECEPTOR ANTAGONISTS
Review round: 2
Reviewer: 1

Output:
Basic reporting: ---
Experimental design: ---
Validity of the findings: ---
Additional comments: Minor suggestions:

Line 80: "liver and adipose tissues are mainly composed of ERalpha". The term "composed" is clearly excessive, something like "mainly include" is acceptable.

Line 346: "as showns". Typo.

Line 604: "as shown in Figure 7". It should be double-checked whether the old or new figure 7 is meant to be cited.


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: LIGHT ALTERS THE IMPACTS OF NITROGEN AND FOLIAR PATHOGENS ON THE PERFORMANCE OF EARLY SUCCESSIONAL TREE SEEDLINGS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The work “Light alters the impacts of nitrogen and foliar pathogens on the performance of early successional tree seedlings” contains interesting information on the early stage of seedling development. The effects of light, nitrogen supply and treatments limiting the influence of fungal pathogens were investigated. The work is well written and easy to read (although as a non-native speaker I do not assess language correctness).
Experimental design: The aims of the work are properly constructed and the methods used allow to verify the hypotheses presented.
Validity of the findings: My main objection pertains the method of determining the degree of leaf damage and the statistical analysis of this feature. The authors wrote that they followed the method of W.C. James (1971) on the basis of which a visual assessment of the degree of damage was made. This method, although it expresses damage as a percentage, does not result in a measurement (continuous scale), only the result is assigned to a specific ordinal category, i.e. the data are expressed in an ordinal scale. This has the consequence that the data cannot be analyzed by ANOVA, even if it has previously been transformed. If the percentage categories had the same ranges, ANOVA could be used, but James did not propose one. Nowadays, when we have computers at our disposal, we perform this type of research with the use of image processing software. In this case, as the research has already been performed, another method of data processing should be used, appropriate for data expressed on an ordinal scale, e.g. a generalized linear model.
Additional comments: My other comments concern Supplementary materials.
Biomass results are reported, but it is not known whether they are in fresh or dry weight.
In the description of the S4 table, the term "day of clipping" appears, which is not mentioned in the current version of the work.


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: LIGHT ALTERS THE IMPACTS OF NITROGEN AND FOLIAR PATHOGENS ON THE PERFORMANCE OF EARLY SUCCESSIONAL TREE SEEDLINGS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is dealing with a contemporary topic of ecological research. Study focusses on interactive impact of resource (light) and disturbance (fungal pathogen pressure) on growth performance of tree seedlings of Liquidambar styraciflua (a shade intolerant species). I think the study was conducted in a deciduous/ dry tropical environment. Measurement were taken continuously for the about 3 months. The data and results are substantial and would enrich the journal content after publication. However, the manuscript is not properly synthesized and the results are not properly discussed in light of literature available from the tree seedling ecology (See: Tripathi SN, Bhadouria R, Srivastava P, Singh R, Raghubanshi AS (2018) The effects of interacting gradient of irradiance and water on seedlings
of five tropical dry forest tree species, Tropical Ecology 59(3): 489-504) .  However, even though this is written with good use of the English language, for which the author is to be commended. Thus, the manuscript needs a major revision before further proceedings. The comments are annotated in attached file.
•	Add, practical implication of the study, in the last line of the abstract
•	In introduction section, you may add some background from dry tropical/ deciduous forest to support your study.
•	Citation of very old studies can be omitted by replacing new studies (delete at least 25% references)
•	Discussion section can be reduced by 30% and should be based only on significant results of the study
•	A separate conclusion section can be added
Thank you for giving me opportunity to review the manuscript.
Experimental design: The experimental layout should be added for easy understanding of the experimental design
Comments are annotated in the attached file
Validity of the findings: no comment
Additional comments: Comments are annotated in the attached file


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: LIGHT ALTERS THE IMPACTS OF NITROGEN AND FOLIAR PATHOGENS ON THE PERFORMANCE OF EARLY SUCCESSIONAL TREE SEEDLINGS
Review round: 1
Reviewer: 3

Output:
Basic reporting: Given the scarcity of information about the mechanisms by which pathogens may contribute to the maintenance of plant community diversity, the data presented in this manuscript have the potential to advance our understanding of plant-pathogen interactions in natural systems. That being said, there are substantial issues with the manuscript in its current state.

The article does not meet standards for clear and unambiguous, professional English. Throughout the manuscript, the following issues exist:
Some of the language is misleading.
For example, L10 states that L. styraciflua seedlings were grown “across a light gradient,” which is misleading because L176-179 state that light levels did not significantly differ between the “high light” and “transect”/intermediate light plots, so all of those data were considered high light in the analyses (i.e., light levels were either high or low in the analyses).
Related the legend for Fig. 1, reports the sample size as N = 32 whole plots and 64 subplots. This is misleading because, while this is not explicitly stated, it appears (based on L176-179) that 88 seedlings were treated as high-light seedlings in the analyses, while only 40 seedlings were treated as low-light seedlings.

Excessive and redundant text. Here are a few examples:
L3: “Shade intolerance may” would be more concise than “This shade tolerance habit may.”
L10: “for approximately three months” can be omitted.
L27: “also may depend critically on” can be shortened.
Paragraphs 1 and 2 of the Introduction are mostly redundant, and should be combined into a single impactful paragraph.
L43-45 could be better organized to eliminate unnecessary and redundant text. For example, “pathogens can limit seedling survival (CITATION), ecosystem productivity (CITATIONS) and species’ ranges (CITATIONS), and can promote diversity (CITATIONS).”
L97-98: Remove all three occurrences of “light” from the parenthetical. It is clear that you are referring to light.
L205: Rearrange the parenthetical so the Tukey HSD is only mentioned once.
L230: “there is a biologically…enemy damage” is unnecessary.
L281-283: Rearrange the sentence so that “field and greenhouse” is only used once.

Much of the text needs to be clearer and more explicit, and terminology needs to be consistent. Here are some examples:
L47: “survival” should be “mortality”
L61-62: “may lose more tissue to disease” than what? Shade-tolerant plant species or shade-intolerant plants in high light?
L62-64: Please clearly state why seedlings would experience more disease when growth is limited. Are you implying that the seedlings cannot escape disease fast enough (e.g., cannot lignify fast enough)?
L68-L69: “susceptibility of SEEDLINGS of an early…. impacted SEEDLING performance”
L77-78: Because survival is the most common metric for seedling performance, prediction 2 would be much clearer with text like this, “impacts on seedling height, a proxy for plant performance, will be.”
L91: Please state why shade-intolerant sweetgum saplings become more abundant near the forest’s edge. I presume this has to do with seed sources and dispersal limitation.
L122-123: Please use consistent and clear terminology for the various treatments used. Specifically related to fungicide application, rather than “enemy damage (high or low)” use “sprayed with fungicide and unsprayed.”
L134 and 136: It would be helpful if the number of seedlings in each treatment was clearly stated (e.g., N = 64).
L155: “impacts on SEEDLINGS”. Try to be more specific throughout the manuscript.
L158: It would be helpful if you stated how much time had elapsed since the seedlings were placed in their treatments (3 weeks). Did any foliar fungal damage occur in the greenhouse? If so, how was this accounted for in the analyses?
L158: Revise language for clarity. “UP TO five leaves per plant”
Details about the Tukey tests are not provided in the Data Analysis section.
L187-190 and the rest of the results section: change “spraying” to “fungicide”. Make sure that each section is interpretable on its own.
L220: Fix the sentence transition because the previous sentence is not fully “in conflict” with the cited studies.
L225: Change “Increasing” to “increased” since you only had 2 nitrogen treatments (high and low).
L287-290: This argument is really hard to follow, in part because of grammatical issues. I had to read it 3 times. Please revise it for clarity and consider splitting the ideas into more than 1 sentence.
L293: “immediate damage” is odd. Do you mean aboveground damage?
L303: Throughout the manuscript, consider using “former pasture” instead of “old field” for the high light treatment. Currently that term is confusing given you also make broader comparisons between the field and greenhouse (e.g., L282-283 and 288).
L322-323: change “plant: to “seedling”

Throughout the manuscript, please improve sentence structure and length, and other general grammatical issues. Here are some examples:
All compound adjectives require hyphens. For example, shade intolerant trees (e.g., L3,5,9) should be shade-intolerant trees (like in L51). Fix throughout the manuscript. Also fix: L38-39 “low nutrient” and L46 “negative density dependent”.
L85: To avoid informal writing, consider “less common as seedlings become increasingly shaded during succession.”
L216-217: This sentence seems to be missing punctuation and a word. “availability, BUT only”
L287: “had also had”

The Introduction, Discussion, and References do not provide sufficient background or context to demonstrate how the work fits into the broader field of knowledge. Here are some examples of relevant concepts and literature that are not, but should be, referenced in the Introduction and Discussion:
L21: Shade tolerance can vary across life stages for a given tree species.
The inhibition of defense compounds and pathogen resistance under low red:far‐red light ratio conditions should be addressed in the Introduction.
L22-23: The trade-off is not explicitly stated.
L52-53 should incorporate/reference Carol Augspurger’s research exploring pathogen impacts in the shaded understory vs. high light gaps.
L57: N limitation is not restricted to temperate forests. See LeBauer, D. S., & Treseder, K. K. (2008). Nitrogen limitation of net primary productivity in terrestrial ecosystems is globally distributed. Ecology, 89(2), 371-379.
L74-75: I am skeptical that this interaction has only been addressed in a few studies given the volume of agricultural literature focused on plant-pathogen interactions. Perhaps that statement is true for natural systems. Either way, the language needs to be modified.
While the manuscript is framed as an exploration of a potential mechanism contributing to succession, the Introduction and Discussion (e.g., in L244-253) should address the possibility that pathogens may reinforce shade tolerance differences among species, thereby enhancing niche differentiation. See McCarthy-Neumann, S., & Kobe, R. K. (2008). Tolerance of soil pathogens co‐varies with shade tolerance across species of tropical tree seedlings. Ecology, 89(7), 1883-1892.
The Discussion section needs to address an additional limitation of this study - that it only explores the effects of pathogens, nutrients, and light for a single shade-intolerant species. The study’s conclusions and central hypotheses about successional dynamics would be much more convincing with additional shade-intolerant species and shade-tolerant species. See Augspurger, C. K. (1984). Light requirements of neotropical tree seedlings: a comparative study of growth and survival. The Journal of Ecology, 777-795. She observed lower pathogen-caused mortality for seedlings of shade-tolerant species in the shade.
L218 needs additional text making a clearer link between the statement and the literature cited. L228 needs additional text making a clearer link between the statement and the literature cited.
L234: low R:FR compromises both salicylic acid‐ and jasmonic acid‐dependent pathogen defenses (de Wit, M. et al. 2013. The Plant Journal, 75: 90-103.)
L244-246: Different aggregation patterns could also be the result of dispersal. This should be addressed.
L244-246: What about the role of belowground pathogens in the observed patterns?
L277-281: The arguments made need additional clarification. “a larger impact on the results” needs to be clearer. On plant growth?
L312-313: Does Pinnus taeda experience relatively lower pathogen pressure? The argument made in L312-313 is incomplete.

While the structure of the article conforms to standard sections, the information contained within these sections, the subsections, and individual sentences needs to be organized in a more logical and readable manner.
The Introduction needs significant revision: improve the organization and clarity of ideas, eliminate redundant text, and improve the context for the study, which will require reviewing and incorporating additional pertinent literature.
The Methods section needs to be better organized. Here are some examples:
L125-127 is an example of a poorly organized, hard to follow sentence. Additionally, “three weeks before the end of the study” is out of place here.
Seedling propagation (L144-153) is near the end of this section, yet it occurred first in the study.
L167-171 Seems more appropriate for the Data Analysis subsection.
The Results and Discussion section would be much easier to follow if they clearly presented each main effect and then their interactions.
L225-230: Improve the readability of the paragraph by eliminating redundant text and rearranging the sentences.
L244-253 Seems better suited for somewhere near the end of the discussion.
L521: These details, “from 8 days after… (73 days),” in Figure 2 are absent from, and should be moved to, the Methods section.

The main text figures are relevant to the content of the article. However:
Fig. 1 should be a two-panel figure depicting fungal damage for seedlings subjected to BOTH fungicide treatments (sprayed and unsprayed), not just unsprayed. The results for the seedlings treated with fungicide should not be buried in the supplement.
The figure legends require revision - eliminate unnecessary details (see L521) and include meaningful sample sizes. Related, “seedlings” would be clearer than “subplots” (L518 and 524).
Experimental design: Yes, this original, primary research falls within Aims and Scope of PeerJ; however, some issues need to be addressed before I would consider the article to be scientifically and methodologically sound (described below).

I have concerns about maintaining seedlings in pots (L100). These seedlings would have been unnaturally suspended above the soil and similar-sized vegetation, which has implications for their exposure to pathogens, particularly splash-dispersed pathogens. At the very least, this needs to be addressed within the Discussion section.

The research questions are reasonably well-defined, relevant & meaningful. It is less clear how this research fills the identified knowledge gap given that it only explores the effects of pathogens, nutrients, and light for a single shade-intolerant species, and to understand the mechanisms shaping succession and heightening niche differences among plant species it is necessary to evaluate additional shade-intolerant species and shade-tolerant species.

The Methods section requires revision. It is extremely hard to follow and there is missing information. These issues make it challenging to assess the scientific merit of the study and the validity of the findings.
Validity of the findings: I questioned the validity of the findings for a few reasons (described below), but I believe that the authors will be able to address my concerns in revision.
The seedlings were in pots (L100), as opposed to being planted in the ground. My concerns about this are described in the “Experimental design” section.
The authors intended to grow L. styraciflua seedlings across a light gradient; however, L176-179 state that light levels did not significantly differ between the “high light” and “transect”/intermediate light plots, so all of those data were considered high light in the analyses (i.e., light levels were either high or low in the analysis). This means 88 seedlings received the high light treatment, while only 40 seedlings received the low light treatment. How did this impact the results? This is not necessarily a disqualifier, but more transparency is needed within the manuscript.
It is unclear whether the statistics used are appropriate. For example, the authors cube root transformed their fungal damage data (L180). Because of the pitfalls associated with data transformation, there has been a shift from data transformation towards the use of non‐normal error structures and generalized linear models. Were generalized linear mixed-effects models considered/used? Were the results similar?
L142: There are separate root and shoot measurements in peerj-49499-Brown_and_Heckman_greenhouse_fungicide_data.csv. If the fungicide affects the root:shoot ratio (which it appears to do based on the root masses), there may be important implications for the plant performance (seedling height) metric.
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: PLASTICS IN PORIFERA: THE OCCURRENCE OF POTENTIAL MICROPLASTICS IN MARINE SPONGES AND SEAWATER FROM BOCAS DEL TORO, PANAMÁ
Review round: 1
Reviewer: 1

Output:
Basic reporting: Overall the writing was good, with pertinent background information, supporting citations, and a central question.

There were a few odd/confusing statements, for example:

"Like sponges, MP is also likely common in the Caribbean" (line 138-139).

The methods section says that "one procedural blank was run along with each of the three water samples" (line 201-202) which I initially interpreted as one blank being run per three water samples, rather than one blank per sample.

In results, would have liked you to report number of PMPs in blanks (for example in line 320)

.
Experimental design: In general, the sample size of 3 for water samples and each sponge species is small. .
Additionally, six procedural blanks for 54 subsamples is not particularly strong. The counts for blanks and sponge samples varied per subsample set (as seen in the raw data, in which there were very few particles counted in samples/blanks in the first subset and greater numbers counted in the second subset.

Why weren't the dry masses of sponge samples more standardized?

The volume used for the water procedural blank samples (1L) would be stronger if it had been the same volume as the water samples (4L).

The microscopy method could have been more clear- how were filters mounted and and how were the measurements conducted?
Validity of the findings: You acknowledge the limitations of the methods in terms of plastic identification and the designation of fluorescent particles as "potential" microplastics. Were any other identification methods attempted (looking for striations, uniform diameter in fibers, or other qualitative properties)? In the discussion, it should be acknowledged that discrepancies between these results and other reported plastic concentrations in seawater may be due to the identification of any fluorescent particle as PMP and not only the sensitive filtration method (line 354-355/line 391). The positive control tests of known plastic types is largely qualitative- it doesn't seem to aid much in the plastic identification in actual samples. Were other non-plastic items tested to determine how they fluoresced?

The introduction states that the size of the ostia generally prevent particles larger than 50um from entering the sponge, yet you found many >50um particles in the sponge. You touch on this in the discussion, how fiber width didn’t exceed 10um (line 421-422), but the mechanism for ingestion of this type of particle is difficult to conceive.

In looking at the metadata file, the blank % in samples as a whole was high- about half of the subsamples had >75% of particles potentially coming from the methodology itself. Is there a significant difference between number of particles in sponge samples vs. the associated blanks?

The metadata file also shows that there were different viewing trials for the water samples that were not described in the methods, with the average taken from viewing trials 2 and 3 (and not 1)? This is unclear.
Additional comments: The study addresses a gap in marine plastics research. The inability to positively identify plastics, the small sample sizes and number of blanks run doesn't provide the strongest evidence, but you are very transparent about the study's limitations and cite other published works using similar techniques.


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: PLASTICS IN PORIFERA: THE OCCURRENCE OF POTENTIAL MICROPLASTICS IN MARINE SPONGES AND SEAWATER FROM BOCAS DEL TORO, PANAMÁ
Review round: 1
Reviewer: 2

Output:
Basic reporting: I commend the authors on submitting a well-written and composed manuscript. The ample citations and clear writing make assessing the content easy and will increase reader comprehension. I’m not sure what the recommendations are for PeerJ, but there are some places where there are a large number of citations listed that may not be necessary, however this is not necessary to change, just something I took notice of.
Experimental design: While the overall design is acceptable, I do have a small concern that I'd like for you to address in the text. The question/hypothesis (what is the prevalence of potential microplastics in sponges and seawater in the Caribbean?) is generalizing across the entire Caribbean sponge population and the nearshore coastal seawater of the Caribbean Sea, yet the samples come from just one location in one area of the Caribbean and may not represent the Caribbean population as a whole (sample does not properly estimate the population parameter of interest as currently phrased). I would caution against extrapolating your conclusions and statements to the entire Caribbean. This location is a sheltered archipelago that is largely outside of the currents and circulation patterns seen in the Caribbean as a whole, and I'd argue that this location should not be used to speculate what the entire Caribbean is experiencing. It's slightly misleading to draw conclusions for the entire Caribbean from a single site. Especially when the standard errors suggest that sample size could be larger to better estimate the population parameter.
Validity of the findings: No comment (but see comment regarding extrapolation to the wider Caribbean above)
Additional comments: Very well-written manuscript, thank you! One suggestion, I'd consider adding the sample size to the figure captions where appropriate (ex. Figure 4) so that the reader knows how many samples are being summarized. Will the data be provided for public use? If yes, consider formatting in long form so that it's easily imported into statistical software.


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: PLASTICS IN PORIFERA: THE OCCURRENCE OF POTENTIAL MICROPLASTICS IN MARINE SPONGES AND SEAWATER FROM BOCAS DEL TORO, PANAMÁ
Review round: 1
Reviewer: 3

Output:
Basic reporting: Overall, the manuscript is well written and the English adequate. However, there are several areas that need to be addressed – detailed below.

A) Units and terminology:
1)	Units throughout are inconsistent. Sometimes you write ‘per liter’ other times ‘L-1’ and other times ‘/L’. I suggest that you use ‘L-1’ and ‘g-1 dry tissue’. Where this occurs, I have highlighted on the marked up PDF. Please change MP/kg to MP kg-1 throughout.
2)	Only use full unit description when at the beginning of a sentence. This is done correctly on Line 184, but incorrectly on line 173 – should read ‘from ~6-8 m below…”..
3)	Please change hour to hr.
4)	Please check all ml are mL to be consistent with L used elsewhere.
5)	Terminology switches between water and seawater. Please use correct prefix when when referring to fresh water or shallow/deep water, waste water etc, and use seawater when referring to the samples collected from the ocean (either in your study or others you are citing). For example,
a.	Line 39 should read “Seawater samples were filtered….”
b.	Line 131 should read “from the surrounding seawater….”
c.	Line 143 should read “in surface seawater…”
d.	Line 184 should read “Four liters of seawater were collected…”
e.	And so on….
This is important as on line 320 “in the water samples or water blanks” it is unclear whether you are referring to a seawater blank or a Milli-Q blank – I presume it should read “in the seawater samples or MilliQ blanks” – please clarify.
Please check the main text and all figures and tables regarding the above – please make everything consistent.

B) Literature references are adequate. However, Please check volume and page numbers of the following references
Avio
Crutzen
Girard
Law

Also, there is a space between Dudek and Easson – might be an issue with citation software, or simply an extra return – please remove.

C) The structure and layout is adequate. Raw data is adequate.

D) Tables and Figures:

Table 1 and Figure 4 should be combined. They show the same data. I suggest keeping Figure 4, but elevating to position of Figure 2. Include the numbers from the table on the graph (or under the sponge name). For the seawater sample add this data to the legend. For example: “For reference, the mean PMP L-1 in seawater samples is 107(+/- 25).”

Also, regarding the dots indicating outliers, these are difficult to see, I suggest changing them to a different symbol, i.e., diamond – as there are no diamond shapes associated with the sponge images.

Please provide full genus name for all sponges. Change water to seawater, and check all units and terminology.

Table 2
In the legend, please provide full genus name for all sponges.

Figure 2
Change to “(percent of total)”. Change water to seawater. Also please provide full genus names for all sponges.

Supplementary Figure 1
I think it would be more appropriate to have the same polymer type together so it is easier to see compare the control vs treatment. For example,

A	a	B	b
C	c	D	d
E	e	F	f
G	g	H	H
I	i	J	j

Also, it would be useful to add titles above the 4 columns.
Water without heat	Bleach and heat	Water without heat	Bleach and heat
Experimental design: General concept and experimental design:

A) Sponge morphology

Line 207: this worries me somewhat. While I understand that you are interested in what is retained within the tissue, the very nature of sponge oscula is that they operate as exhalant pores discharging water and items from the spongocoel to the outside – so you may potentially be washing away particles that the sponge is actively discharging at the time of collection. Perhaps a future experiment could focus on collecting this discharge and looking for MP.

Line 443 mentions differences in PMP concentration across the species but there is no in depth discussion (other than for fibres) of the size classes and how they relate to ostia size of each species. Please consider the morphology of the six sponge species investigated (i.e., size of oscula between species) and how this compares to the PMP loads found within them.

Following on from this…
Line 262: Particles are sorted into 9 size ranges. Please provide an explanation as to why these categories are important – do they correspond to the diameter of osita/oscula in the various species investigated?

B) Background contamination

Line 216: not pre-filtering solutions prior to use, especially household bleach that likely comes in a plastic container (the authors do not provide any detail) is a significant flaw in this study. Even though the authors go to great lengths to state this limitation upfront and in their results section (line 334-338), I have very little confidence in the results.

Line 520: your results show it is imperative that filtering of ALL solutions be done, otherwise you cannot trust your results, which unfortunately is the outcome of this study.
To overcome this a net correction was done. Should you have used a chemical method such as Raman or FTIR, you would have been able to identify the polymer type and only exclude those that were found in both blank and sample (see F. Kroon, C. Motti, S. Talbot, P. Sobral, M. Puotinen, A workﬂow for improving estimates of microplastic contamination in marine waters: A case study from North-Western Australia, Environmental Pollution, 238 (2018) 26-38.). I am presuming that access to such equipment was not possible at the time this work was conducted, in which case the authors need to include:
1) a statement in the introduction or methods regarding the choice of technique, i.e., as a first screen of samples to identify PMP for further analysis,
2) a statement in the discussion strongly recommending that FTIR or Raman be used for future studies to confirm the findings presented here. If the samples are still available it would be worth analysing them by one of these methods and comparing the PMP found here with those confirmed to be MP by chemical analysis.

C) Polymer characterisation

Fluorescence microscopy, especially how it is applied here, has limited capacity to establish an item as a polymer. It can help to detect MP within a sample (i.e., to screen samples and identify those that should be further characterised) but cannot identify the type of plastic polymer. Techniques such as Raman, FTIR, MS are needed to confirm chemical composition. The authors need to state this more strongly. Results reported on Line 305 highlight this, with some polymers able to be detected based on their fluorescence, while others not. The authors show their method of choice is limited – but offer no alternative method of verification.

Line 508: the authors again state the limitations of this fluorescence method to detect MP, and mention brightfield microscopy – was this method used by the authors as a secondary method of PMP identification?

Also please read Monteleone et al 2021 https://doi.org/10.1016/j.jece.2020.104769
Validity of the findings: I have reservations about the PMP loadings found, and specifically the emphasis placed on them likely being MP, given they did not filter the bleach before using. The authors are transparent in this, and with hindsight I have no doubt pre-filtering of ALL solvents used will be incorporated into any future study they undertake (a lesson learned). However, given the plethora of studies now published that have focused on improving workflow practices and eliminating or accounting for background contamination, the lack of implementation of pre-filtering is of concern, i.e., suggests the authors were not familiar with the literature BEFORE conducting the experiment.
The authors need to address this and the other issues I've raised.
Additional comments: Comments on the text

Abstract:
Line 46: There is no information provided in the abstract that indicates the 'resistance'. Please reconsider this phrase or delete.

Introduction:

Line 56: Please be careful here, nutrients and sediments are natural. If you are referring to land runoff and fertilizers then state that explicitly, i.e., “The detrimental effects of anthropogenic pollutants such as chemicals (provide examples in brackets – wastewater discharge, oil spills, etc), nutrients from fertilizers, and sediment from land runoff on the environment are well known…”

Line 57: the release of microplastics IS of great concern – we are currently worried, so be stronger in this statement. For example “but the rapid proliferation of microplastic (MP) contamination is now an issue of increasing concern”

Line 64: change degradation to fragmentation.

Line 75: change to “the overall impact of MP”. The use of ‘role’ suggests it is part of the system – MP are NOT natural and do not belong, so they impact.
Line 78-82: please place each citation after the organism type – some readers may be interested in a specific organism and would appreciate being directed to the appropriate citation.

Line 108: change to “The removal of these food particles from the water column by sponges…”

Line 112: Please elaborate on the ‘widespread distribution’. Sponges have a broad spatial and temporal distribution, with many varied habitats, i.e. from mangroves, tidal pools, coral reefs, CO2 seeps, deep water, cold water….

Line 157: write ‘as per Covernton’. Also by your definition items are not MP but PMP so please modify this sentence. I suggest “We used fluorescence microscopy to identify and quantify potential MP (PMP) as per Covernton et al. (2019).”

Materials & Methods:

Line 185: Please change one-liter to 1 L (same for Line 373). Also how were the 1 L glass jars cleaned? It is important to provide such details, especially as background contamination is such an issue in this type of research.

Line 197: please explain what analytical grade water is – reverse osmosis? Milli-Q? Purchased from a supplier? Has it been filtered, if show what range filter size? Same comment applies to Line 281.

Line 201: Suggest you change this to “One procedural blank was run in parallel to each of the three seawater samples”

Line 215: change ‘shows’ to ‘causes’

Line 219: change to “to evaluate the degree of pre-existing experimental contamination.”

Line 219: Please change to “Vials with sponge tissue were heated to 60°C for 2 hr to expedite digestion.” Also, please provide references to support the use of bleach and heating to recover MP. Bleach is a strong oxidising agent and can damage some plastics, heat is known to exacerbate (or accelerate) chemical reactions. And include reference to the section “Positive Controls” specifically instead of saying (see below).

Line 240: the term “others” is used – please consider a more appropriate name. For example, ‘unknown polymer’ (Punknown). “Others” is very unscientific.

Line 243: Please rephrase this – it is clumsy. I suggest “Two controls (without MP added) were also included. The first was bleach digestion (X mL) with heat (N=10) and replicates were processed according to the sponge sample procedure. The second was MilliQ (X mL) without heat (N=10).” Its not clear to me how these were then processed – by adding an additional 5-10 mL? or simply filtered?

Line 253-254: this sentence reads like a result. I suggest rephrasing and providing relevant citations. For example:
“Potential MP was distinguished from fluorescing background material based on the brightness and color of fluorescence. Inorganic sand grains, proteinaceous spongin, invertebrate cuticle fragments, etc, generally emit a dull, blue-green fluorescence while many plastics fluoresce stronger and with an electric blue color (Figs. 2, S1) (citations)”.

Line 255-258: these two sentences seem to be saying the same thing. Please clarify. If they are a duplication then please combine, if not then please provide further explanation. Also were PMP assessed using standard stereomicroscopy (to determine true color, and also texture)? If so, then details of this needs to be included here. Visual assessment as a component of MP characterisation is widely used –

For visual assessment see F. Noren, Small plastic particles in Swedish West Coast waters,  N-research, Internasjonale Miljøorganisasjon (KIMO), Lysekil, Sweden, 2007

For visual assessment within a workflow see F. Kroon, C. Motti, S. Talbot, P. Sobral, M. Puotinen, A workﬂow for improving estimates of microplastic contamination in marine waters: A case study from North-Western Australia, Environmental Pollution, 238 (2018) 26-38.

Line 288-291: this is repeating information from line 212. Please delete from here and combine with line 212. There is no need to remind the reader.
For line 212 I suggest: “Each subsample was cut into pieces with a utility blade and added to a clean 20 ml glass scintillation vial and covered with foil. In total, 54 subsamples were generated (6 species × 3 replicates × 3 subsamples).”
And then for Data analysis I suggest “The blank-corrected number of PMP g-1 was determined for each of the 54 subsamples representing the six species”.

Line 295: please cite R correctly, including the version used. Refer to https://rdrr.io/r/utils/citation.html

Line 305: “PETE, Polyester” Polyester is PETE!

Results:

Line 310: Please change to “Exposure to bleach and heat did not impact on plastic fluorescence behavior (Fig. S1).”

Line 315: please change to “comprised ~25% of…”, similarly for line 316 “, with ~27% of all particles…”

Line 332: please change to “(17 of the 54…”

Line 340-343: these sentences are confusing. You state that “Most PMP found in all sponge samples…” Yet in the preceding paragraph you stated that 17 subsamples returned a -ve net value, so not every sponge had PMP present. Please clarify.
I presume you mean: “PMP found in sponge subsamples and blanks were mostly very small (10-20 m), comprising nearly half of the total number of PMP detected. These were mostly found in A. cauliformis, A. compressa, C. vaginalis, M. laevis and the blanks, while only 32% and 25% of very small particles were found in I. campana and N. erecta, respectively (Fig. 3).”

Line 343: Please change to “Together, very large particles, small fibers (501–1000 μm) and medium fibers (1001–3000 μm) comprised a large percent (~25–31%) of the total number of particles in I. campana, M. laevis, N. erecta, but not in the other species or blanks (Fig. 3).”

Line 347: please change to “were found only in sponge samples….”

Discussion:

Line 355: Please change to “These previous studies…”

Line 374 and Line 383: Line 383 repeats information on line 374. Please revise so there is minimal repetition. I suggest for Line 383 “Covernton et al (2019) reported 5.28 MP L-1 from 8-m filtered surface seawater samples in coastal British Columbia”.

Line 379: You state “The authors highlighted the necessity of using bulk seawater samples and sensitive filtration methods (ability to detect plastics down to 10 μm) when assessing the exposure of marine organisms to MP pollution (Covernton et al., 2019).” Terminology is very important here. Sensitive filtration methods do NOT give the ability to DETECT plastics, rather to collect MP down to 10 m. Only chemical techniques can detect plastics.

Line 387: Please change to “Although our subsurface value of 107 PMP L-1 corroborates Norén & Naustvoll (2010), it is elevated compared to the other studies.”

Line 398: change to “indicate that they do ingest MP”

Line 399: This is a little confusing. I presume you mean “Raman spectroscopy of items recovered from tropical sponges of Indonesia, digested with bleach and filtered over 1 m membranes, revealed the presence of naturally occurring items such as minerals and shell fragments, as well as anthropogenic items (91-612 PMP g-1 dry tissue; 5-200 m) including cotton and polystyrene (Girard 2020). Of note was one sponge, Ircinia sp., which was found to have 159 polystyrene MP g-1 dry tissue.”

Line 423: change to “within the bodies of the six sponge species…”

Line 440: There is a wealth of information available regarding sponge egestion of particles (shells, minerals of similar size range to MP) – surely this information could inform the potential of your species to egest the MPs, even though MP egestion itself may not have been investigated.

Line 451: agree that particle spatial variation is an important factor, however, so is the preferred size spectrum of the sponge.

Line 457: agree, but should also investigate relationships between these six species from sites that are considered to be more and less contaminated with MP. That would really confirm that they are simply filtering and not selecting for MP.

Line 468: this statement is only true if the gastrointestinal tract and contents is consumed. There is next to no evidence of plastic contamination in flesh, although there is evidence of other chemicals such as plasticisers in flesh. Please provide some detail to support this statement, or if the GIT is not eaten, then better to simply remove any reference to seafood consumption.
I suggest “…susceptible to MP ingestion. With entry of MP into local waterways expected to increase as tourism and residency rates continue to increase, this risk to marine species will be exacerbated (refs).”

Line 483: Please change to “These values are far greater than the 8,000 PMP we predict to be present in a sponge at any given moment in time.”

Line 488: please change to “we did not detect any external effect…”

Line 490: please change to “of effect, with MP exposure having little impact”

Line 492: yes, it maybe that they can resist MP ingestion, or it maybe that they have the ability to increase the egestion rate if the particle load within the spongocoel reaches a threshold. See McGrath 2017 https://doi.org/10.1016/j.jembe.2017.07.013. Note however, there is a threshold of sediment load after which the sponge is likely to not be able to egest, and health begins to suffer. See Pineda 2017 https://www.nature.com/articles/s41598-017-05251-x.

Line 497: please change to “resistant specifically to MP exposure…”

Line 514: given you are likely underestimating the MP presence you cant really say that sponges are resistant to MP uptake – you need to state this again.

Line 537: bleach and heating is known to affect some plastics – just look up any on-line compatibility chart. Also, please note that the extent of the effect was assessed by fluorescence microscopy only – it may be that the polymer integrity is impacted on a chemical 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: PLASTICS IN PORIFERA: THE OCCURRENCE OF POTENTIAL MICROPLASTICS IN MARINE SPONGES AND SEAWATER FROM BOCAS DEL TORO, PANAMÁ
Review round: 2
Reviewer: 1

Output:
Basic reporting: I commend the author on providing a thorough and detailed review of the literature and providing pertinent background information. On second review, I noticed a few instances of providing almost too much detail, superfluous language, and over-use of parentheses in some cases.

Line 34: starting with “This is surprising…” could be reconfigured to avoid use of that type of terminology

After defining PMP, refer to all following instances with the same. Line 40 says ‘to retain any MP present” and lines 42 and 165 uses “potential MP”

Line 98: “Prolific” here can be eliminated. Just state that sponges often exhibit high pumping rates

Line 136: Delete “also”

Lines 152-153: Not sure it is necessary to include detail on symbiont derived nutrition

Lines 177-178: Exclude “also” from both sentences

Lines 245-146: Do you need the parentheses?

Lines 281-282: I don’t think the parenthetical information is important to include “(the length of the 10x10 grid was equal to 1 mm…)”

Lines 337: You used a different spelling of fluorescent here compared to elsewhere in paper.

Line 348: Reconfigure sentence to avoid use of parentheses.

Lines 359-361:  Reconfigure sentence to avoid use of parentheses.

Line 383-384: Try to avoid parentheses here too

Line 454: replace method with mechanism

Line 526: “Elevated” is an odd word choice. Elevated as compared to what?

Lines 528-529: Could be abbreviated to “and other coral reef associated marine invertebrates”
Experimental design: The overall description of the methods has been improved. Here are my additional comments:

Methods, data analysis: Why weren’t the water filters blank corrected?

Methods data analysis: Lines 319-321 are confusing. From what I understand, for each species, you collected samples from 3 individuals. Then you broke each individual sample into 3 vials for digestion. Wouldn’t you add the counts from the 3 vials as they are part of one sample, rather than taking the average?
Validity of the findings: While you are, again, very transparent about the limitations of your methodology, I'm not sure this is reflected properly in the extrapolation of results. In general, I would edit the discussion to be even more cautious with your assumptions. Examples include:

Lines 276-280: The variation in counts between different surveys is concerning and doesn’t instill confidence in an accurate count in seawater

Lines 425-429: My biggest concern with this paper is the broad interpretation of the results. Such as in this case, you first you state that your study suggests that sponges ingest MP. Then the next sentence says that you can only tentatively report potential MP in sponge samples, making the first sentence an overstatement.

Lines 535-549: This paragraph is an extrapolation built upon already provisional results. I don’t think it should be included.

Lines 574-575; 579-580: Make it clear that while your methods may miss certain plastic types, they also may be positively skewed by non-plastic fluorescent particles.

Line 617: “Our results further indicate that sponges do ingest MP” ignores the “potential” part of PMP. Rather, they ingest fluorescent particles that resemble MPs
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: FLATFOOT IN AFRICA, THE CIRRIPEDE CHTHAMALUS IN THE WEST INDIAN OCEAN
Review round: 1
Reviewer: 1

Output:
Basic reporting: This paper set out to describe the phylogeography of chthamalid barnacles from the West Indian ocean. The authors use morphological descriptions derived from LM, SEM, and macro images in combination with molecular markers (COI and NaKA). Four species-level clades were found in the WIO and adjacent waters, including one new species, the Madagascar-endemic C. barilani. This species is described in good detail. C. malayensis is found to harbor four genetically separated clades/clusters and it is concluded that these are four putatively cryptic species (or one? See below). The authors morphologically describe, and amplified, the four species clusters from the WIO and argue that their relationships differ from other accounts of these species.

I liked that the authors strived to integrate several data layers and that they also discuss dispersal potential. However, the overall readability and coherence of the manuscript need to be substantially improved. At present, it is really difficult to understand what the authors do and why. I have commented on this in detail below.

Front page and abstract:

Author list: Why are the two first authors having different affiliations? 1 and 2 appear to be the same institution.

“.. are key inhabitants of rocky intertidal shores”: There is no reports on the ecological importance of these barnacles. We may surmise that they must play some role in the ecosystem, but every species plays a role. I don’t support this sentence. “Key” is too broad and not supported by empirical data nor experiments. I suggest writing “wide-spread” or “commonly encountered”

“.. which was found in Madagascar”: Is this new species only found there? In that case, it would be nice to mention that it is a new endemic species.

“C. malayensis comprises a group of four genetically differentiated clades
representing four cryptic species. The newly identified African clade is genetically different from these clades and the pairwise distances between them justify the conclusion that it is an additional cryptic species of C. malayensis”. I am not sure what the authors mean. What is “it is an additional cryptic species”? I thought the authors argued for four cryptic species. Please elaborate or rephrase more clearly.

“This represents the East Northern...”: Northeastern

“merely on morphological data”: Suggest substituting merely with “solely”

“correct taxonomy”: What is correct taxonomy? The taxonomy of species is a continuum and claiming that COI, NaKa and a limited set of morphological characters reveals the universally true taxonomy is probably an oversimplification. How about writing for “…combination of morphology and phylogenetics in barnacle taxonomy”?

Introduction:

L56: I am not convinced that the species are “key inhabitants”. Explain more or provide concrete evidence. Alternatively, write “some of the most commonly encountered intertidal barnacles with a worldwide distribution”.

L57: Darwin wrote four monographs and the one cited is just one of them. It is not a big deal but maybe write “in his monumental monograph on extant acorn barnacles”.

L60: Chthmalinae is currently challenged. Perez-Losada et al. (2012) clearly showed that neither Euraphinae, Chthamalinae, nor Notochthamalinae is monophyletic. Suggest writing either “of the paraphyletic subfamily Chthmalinae” or “of the family Chthmalidae”

L61: Chan et al. (2021; Zoological Journal Linnean Society) recovered 27 species of the genus. Can the authors elaborate on that discrepancy?

L72: East coast?

L91: Suggest adding this statement at the end of the sentence: “…. , although several taxa (from the entire class Thecostraca to subfamilies) are essentially only recognized by molecular analyses (Chan et al. 2021)”. Many barnacle taxa are only monophyletic by molecular analyses.

L94: “of morphological variants different species”. Suggest rewriting or just writing “morphologically different species”

L97: “growth, (mainly opercular),” . Delete comma between growth and ( )

L98: “arthropod appendages” . Suggest writing “segmented”

L99: “distinguish variants, over the past” . Change the comma to a full stop.

L100-101: Why only this reference? Chan et al. 2021 is the most recent and most comprehensive account to date. The studies by Perez-Losada (2001, 2002, 2009, 2012, 2014) should also be cited since they are important contributions.

L103: “of Chthamalid barnacles”. Write chthamalid

L107: “this part of the ocean revealed” . Which ocean? The Ocean in general? Or “these seas”? or “oceans? I am confused.

L116: “Skeletal structures” . What is meant by this statement? The exoskeleton? Or the “shell plates” which are not skeletal by any means.

L129: “according to the manufacturer’s protocol” . This is a very standard way of writing and I am aware that every study using DNA extraction writes it this way. I just don’t like it. Please emphasize that you followed that protocol exactly so that others can repeat the experiment. I can appreciate it if the authors want to keep their statement as it is indeed a standard statement.

L131: “a partial CDS”. Please define CDS

L133-138: “barcode primers LCO1490 and HCO2198 (Folmer et al., 1994) and the primers of Wares et al. (2009)”. Please be more specific. Either use a table or spell out the exact primer sequences, the annealing temperatures, extension temperatures, number of cycles, and volumes used in the PCR reactions including the amount of input DNA. Please also note that you carefully checked (i.e., translated) the obtained COI sequenced. Co-amplifying Nuclear mitochondrial pseudogenes lead to spurious species assignments. It is not universally true that NUMTs possess truncated protein structures or stop codons, but still, it is usually a pretty good indicator that a NUMT was co-amplified if the COI sequence has stop codon(s).

L142: “selected by MEGA.” . Which models? Nucleotide substitution models? Which model(s) was/were chosen? Did MEGA choose the model based on the AIC or BIC criterion? In this case, two different models were chosen by the two criteria, which one did MEGA or you select? For such a shallow phylogeny, it may be OK not to list this. On the other hand, attention to detail matters. (OK I see you put it in the results section. Good!)

L154: “as well as randomly selected sequences”. What do you mean by randomly selected? Why would you ever randomly select sequences for a phylogeny?

L173: “compared because of high variability” . High variability of “what”?

L178: “recorded Chthamalid” . Write chthamalid

L190: “and Chthamalus Alani” . alani

L194: “Chthamalus proteus” . C. proteus

L221: Chthamalinae has been abandoned. See Chan et al. (2021)

L321: “Examination of arthropodal characters”. This is too vague. Define the characters more clearly.

L351: “sea from the eastern coast of”. Eastern

L350-367: This section is not Results but Discussion. Please relocate. I see that you have united results and a short discussion under each species. It may be OK. Consult the editor. I think a single Discussion section is better.

L352: “This hypothesis could be supported by the dispersal of lecithotrophic larvae across” . Chthamalid barnacles have planktotrophic nauplii that develop over 2-3 weeks (Yan and Chan JMBA UK). In fact, had the development been lecithotrophic, we would not expect “vast dispersal”.

L358: “and west Indian”. West Indian. Check this carefully throughout the MS

L359: “adjacent sea”. What do you mean? “seas”?

L385: “The populations were therefore, these populations were grouped under C. cf. challengeri”. Please rephrase

L412: “along the southern and eastern coasts”. Southern and Eastern

L443: “There are clades that cluster species from different groups; for example, C. stellatus and C. montagui on the same clade.” Please rephrase. “Clades cluster species from different groups on the same clade”. Slightly confusing.

L453: “Chthamalu. montagui” . Chthamalus montagui.

L455: “that the “challengeri”. Italicize challengeri

TABLES in general:
I would convert this table into a pair-wise genetic mismatch frequency table. That way the authors can more easily inspect intra- and interspecific thresholds and cut-off values between and within species.

Are the pairwise genetic distances between species significantly different from each other? Maybe this is not the best way to study species delimitation. I am no expert in this field.

TABLE 1:

I would convert this table into a pair-wise genetic mismatch frequency table. That way the authors can more easily inspect intra and interspecific thresholds and cut-off values between and within species.

C. barilani is not in italics in the first row

Is “values” = “differences”?

TABLE 2:

Please define abbreviations

FIGURE 1:

This photo plate could have been more aesthetic. The images have to align and the frames have to be horizontal/vertical and not “skewed” as here. The scale bars are “floating” in different places in the pictures. I suggest placing them at equal distances from the picture frames. The coloring of the background could have been optimized for Fig 1 C and D. There are still some white margins here and there. Maybe give these two images another round of polishing?

FIGURE 2: Please spell out WIO. Maybe mention the total bp alignment that was used to construct this tree.

Did the authors try other mitochondrial or even nuclear markers? I am surprised to see the low support values of COI at this taxonomic scale. Maybe 16S or even 28S and a concatenated alignment of either COI+NaKA or COI+NaKA+16S+28s would be needed to fully resolve the sister relationships of the clades? This is not a “make or break” requirement for publication but would surely be nice.

The authors could insert the pictures of the species on the phylogeny. Would be a bit easier to appreciate their differences then. It seems there is space enough around the clades.

FIGURE 3:

Please insert the legend from Fig 2 as well. Difficult to scroll back to Fig 2 for checking which annotations belong to which species

FIGURE 4:

Suggest making the frames of equal size. This can be done by inserting a white line of equal size between the aligned images. The 0.5 and 3.0 text pieces appear to me as different fonts. Please ensure that the same font is used throughout. The lower right corner of Fig 4B has not been darkened entirely. Suggest painting that area black. There is a tiny piece of black that exceeds the width of the figure in Fig C. Suggest trimming the edges of the figure.

FIGURE 5:

Was the same font as in other figures used? Suggest standardizing font sizes and types.

FIGURE 6:

The scale bar outline is different in this figure from other figures. Suggest standardizing how the scale bar is drawn.

FIGURE 7:

Why are there extra white scale bars in A, B, C, and F? What happened to F? The lower right corner of F does not look so good neither does the gray-scaled scale bar. Suggest standardizing images. The sizes of the frames are not equal. Please optimize this.

FIGURE 8:

The figure letters and scale bars are floating freely around and not at a standardized distance from the edges. Frame and images sizes are not equal. Please optimize this.

FIGURE 9:

It is OK 8 (good in fact) that B was cut in the lower-left corner to harbor C. But please make an effort to standardize frame sizes. The figures look, to me, very sloppy. The scale bars are not of equal size, font, and type. In C and E there are two scale bars.

FIGURE 10:

This is also a sloppy figure and requires substantial edits. Make frame sizes equal. Make sure image edges are aligned. Make sure that scale bars are aligned and of the same width/size. C is thick and white. A and B are thin and black. The scale bar in C is covering the material, but it looks like the scale bar in A was deliberately place above the Cirrus I. Why this putative discrepancy? E covers D without a frame. This should really be optimized with equal frame sizes. Why is there suddenly a black frame around a white scale bar?

FIGURE 11:

Are those numbers indicating support values? I am surprised to see them so low at the “backbone”. Maybe the authors should either attempt to concatenate NaKa and COI or add maybe 16S, 18S, 28S or H3 sequences additionally to get enhanced resolution? Although the species level resolution looks fine, the low support values matter for the bigger picture. I am curious as to why the species assembly shown here was not included in Fig 4? The relationships appear different. Why? This highlights why a separate discussion is warranted.
Experimental design: The experimental design is principally OK. I understand why COI was chosen as the species delimiting marker. I would encourage the authors to argue why NaKa was chosen as a marker over e.g., 16S or a nuclear ribosomal gene? Clearly, COI alone cannot distinguish the backbone of the family, so maybe an extra gene and concatenated trees are needed. Such additional sequencing not “make or break” but would improve the paper. There are balanomorphan specific 16S primers in the literature. John Wares has used EF-1a on Chthamaloids. Maybe it is worth using these primers for also including some of his specimens as outgroup/ingroup?

It is nice to see that both macro, LM, and SEM imaging are being used.
Validity of the findings: The authors resolve the phylogeography of Chthamalid barnacles in the Western Indian Ocean (WIO). However, the potential impacts of the low support values need to be discussed more upfront. I suggest writing a separate discussion section where phylogeographical patterns are discussed in greater depth and also in the light of the dispersal potential of the species (the authors already initiated an interesting discussion on this). The authors already commented on this, which I really liked (although they misinterpreted the development as lecithotrophic, which in fact is planktotrophic).

I would also like to see a deeper discussion on the morphological differences. The authors write several places that “arthropodal characters”, “morphological features” or “morphology” agree with the molecular monophyly of species. What are these characters specifically? It is fine that the species are described in detail but this is done in a telegraphic language that is extremely difficult to compare between species in the text. Since none of the important morphological characters, as listed by the authors, appears on the phylogeny or in a table, it is extremely difficult to compare and assess the differences. I suggest the authors to make a table of key differences in shell, feeding apparatus, trophi and/or other structures that are commonly used to distinguish the barnacles studied. It is at present really difficult to assess how the authors handle differences between gene trees, “morphology” and the somewhat different tree in Fig 11.

The “species delimitation” of WIO species seems to hold and appears valid enough although a broader discussion of the COI+NaKA+morphology approach needs to be further discussed, I think. Many other papers used nuclear and other mitochondrial markers on chthamaloids and come to different genus-level relationships. I am slightly confused by the differences between Fig 4 and Fig 11. I am not an expert in chthamaloids so maybe the authors can explain these differences? I did not fully understand the purpose of Fig 11. The authors write that “However, the conformity between the phylogenetic tree (Fig. 11) and the grouping based on morphological parameters is only partial”. So Fig 11 is intending to challenge the discrepancy between morphology and genetic markers? Or? I do not fully understand how this, particularly when thinking of the overall purpose of the paper which again is to resolve phylogeography of WIO chthamalid barnacles.

I would therefore have liked to see a broader discussion of how different approaches and models may affect the phylogeographic assessment.
Additional comments: Already given above.