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: IMPERVIOUS SURFACE AND LOCAL ABIOTIC CONDITIONS INFLUENCE ARTHROPOD COMMUNITIES WITHIN URBAN GREENSPACES
Review round: 2
Reviewer: 3

Output:
Basic reporting: I thank the authors for their work on the revised version of the manuscript. Several sections have been improved and most of the comments were addressed. The main change is that arthropods were identified to morphospecies, which allows for a more detailed analysis. Also, I see clear improvements in the introduction, the delineation of their goals, and the description of the study sites. Nevertheless, I think that a few major things remain unclear and I also listed several minor comments. I am sorry that I cannot recommend your manuscript for publication in its current state, but I am convinced that these changes will improve the quality of your work. I look forward to reading the revised version of your paper.

Major comments:
-Regarding analyses, I am still not fully convinced about the approach they used. As mentioned in the first revision, fitting models with more than one predictor is a standard practice in ecology. If the authors are convinced that fitting simple univariate models is better for a particular reason, I think this should be clear in the methods and supported by a reference. At the same time, the rebuttal letter indicates that when equivalent models were detected, an additive model was tested but this is not mentioned in the manuscript or reported in the results. Therefore, please expand this section by stating exactly what you did and report the models in your tables. Even if the additive models are not better, I would still want to see their estimates and details. In connection with analyses.
In the revised version, the authors have included site type as a predictor after the suggestions, but this was also done in a univariate model. This can be seen in the tables, but not in the R code, please check that. My point is that site type is not an urbanization/habitat variable as the remaining factors, but a variable that is inherent in your study sites. Thus, I believe that site type should be always included as a predictor in addition to any other variable, in order to contemplate the design of your study.
Finally, the authors stated that they used GLMs, but the R code shows that for both abundance (log-transformed) and diversity, LMs with Gaussian distribution is used. Was morphospecies richness analysed using a Poisson distribution? As the R code includes only the first two response variables, this is not clear. Also, why use log-transformed data when negative binomial GLMs are good for dealing with abundance data? Please explain the distributions used for each response variable and justify the transformation for abundance.
-In connection with my comment on study sites, Permanova showed that this variable had a marginally significant influence on the community composition and I think it should also be included in the final model. I repeat my original comment that including the study sites in the NMDS using the same symbols as in Fig. 1 will help to better understand how different was the composition between gardens and prairies.
-In the results section, table S2 shows that morphospecies richness was negatively linked to purple flowers, even though this model was similar to the null model in terms of AICc. Even if this means that the support from the data was weak, I think this should be reported and discussed as well.
-The title and discussion emphasize that abiotic conditions are influencing the responses of insects, but keep in mind that impervious cover effects can reflect the negative effects of losing green habitats. In other words, can you be sure that this is entirely an abiotic driver, or could the low availability of green spaces (biotic factor) explain your result? Most of the results are linked to temperature and humidity, but still, you could be more cautious about that response to impervious cover.

Minor comments:
-L 52: perhaps obligatory is not the best word to describe these ecosystem services? Essential or needed?
-L 76-78: McGlynn et al worked with only one diverse family, so I think this sentence should not be so general. Also, the specific group studied by Andrade et al is missing.
-L 106-107: here it should be clearer that 8 gardens and 8 prairies were sampled, it is not completely clear in the text.
-Table S2 is hard to read due to the line formatting. I suggest using horizontal lines or different background colours to separate different response variables.
-Table S2: what do the estimate of site type reflects? Were gardens the reference level?
-L 188-190: by individuals you mean flowers? Please modify this, individual flowers are not directly linked to individual plants.
-In connection to my previous comment, which criteria did you use for counting inflorescences? Were they counted as one flower?
-L 193 and 204: I think the word results is not needed for these two sub-headings.
-L 201: it should be white flowers.
-Table 2: following the same logic as in the response variable shown here, I think that for the remaining response variables the null model should be listed if it was the best one.
-L 235-237: this point highlights that garden could be more humid than prairies and thus site and humidity should be included in the same model to disentangle their influences.
-L 263: underlie.
-Fig. 3 and 4: are the plotted regression lines the ones fitted in the models, or simple lines added to the raw, untransformed data? I think this should be clearer in the legend and I insist that adding confidence intervals would be better to visualize the responses of arthropods.
Experimental design: All comments are included in basic reporting.
Validity of the findings: All comments are included in basic reporting.
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: IMPERVIOUS SURFACE AND LOCAL ABIOTIC CONDITIONS INFLUENCE ARTHROPOD COMMUNITIES WITHIN URBAN GREENSPACES
Review round: 3
Reviewer: 1

Output:
Basic reporting: This new version of the manuscript has improved a lot. I appreciate the effort of the authors. I suggested only minor changes below detailed.

Abstract
-First sentences: Please use a synonymous in order to not repeat so many times the word decline
-Line 18. replace for few studies in cities
-Lines 19-22. Reframe these two sentences, they are repetitive:  In this study, we surveyed arthropod communities within a medium-sized, growing city. We investigated arthropod communities (abundance, richness, diversity, community composition) within urban greenspaces across metropolitan Grand Rapids, Michigan (USA).
-Line 23. Be more specific about which environmental variables are you considering
Introduction
Line 64. where it says “as specialist species are replaced…” should be added "native"
Line 69. add an “s” to animal
Line 98. Please be more precise regarding which environmental variables you evaluated
Material & Methods
Line 110. Where it says “but often contained non-edible flowers” shouldn´t be vegetables?
Line 151. Correct to: The percent of impervious
Line 152. It is rare the expression “percent developed imperviousness layer”, revisit it
Line 168. It should be GLMs
Lines 172-173. I am still not quite convinced about first testing each environmental variable separately, but I agree that this section has improved a lot.
Line 180. You said “made adjustments by altering family distributions”, please be more precise referring to which distribution did you used
Discussion
Lines 234-236. Please re-write this sentence, it is not clear what did these variables have an effect on?
Line 243. Correct to: impacts of urbanization
Line 313. Replace: “we recommend future studies” to “future studies to identify floral species in lieu of using floral colors as environmental factors should be necessary” in order to be not repetitive with the term recommend
Experimental design: detailed before
Validity of the findings: detailed before
Additional comments: detailed before


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: IMPERVIOUS SURFACE AND LOCAL ABIOTIC CONDITIONS INFLUENCE ARTHROPOD COMMUNITIES WITHIN URBAN GREENSPACES
Review round: 3
Reviewer: 2

Output:
Basic reporting: Thank you for revising your article and following the comments made on the previous version. I believe the article has improved considerably and it is much closer to, in my opinion, being accepted for publication. The methods and the figures are now clearer. I only have a few minor comments to report.

-L 175: the model selection description mentions that models within 2 AICc units were considered equivalent, but for several groups (especially for morphospecies richness) the null model and other models had similar AICc values, but only the null model is reported in Table 2. I believe that either every model with the deltaAICc = 2 should be reported there or that sentence in methods should clarify that if the null model had the lowest AICc value the selection process was different.
-L 175-179: thanks for including the additive and interactive models in the supplementary material. Even though I agree that interactive models can be problematic when doing model averaging, additive models are usually ok and the authors are not doing model averaging in their work, so the statement may not be necessary. Personally, I would have analysed the data differently by fitting additive models including all the possible combinations of predictors, but given that the authors provided suitable references for their choice I can accept it if the editor approves it.
-L 217: perhaps a better sub-heading could be used for this section. One that is not focused on the method you used, but on the responses of arthropods to the factors you studied.
-L 234-236: with univariate responses you mean the responses of each order? Please clarify. Also, the sentence could be better connected with the previous one.
Experimental design: See 1.
Validity of the findings: See 1.
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: ANTIMICROBIAL PEPTIDES PROPERTIES BEYOND GROWTH INHIBITION AND BACTERIAL KILLING
Review round: 1
Reviewer: 1

Output:
Basic reporting: The article is very well written and clear, It deserves the addition of a table, it would complement the article.
I recommend that the table contain the peptides that inhibit
biofilm formation at sub-inhibitory concentrations of growth, peptide sequence, mechanisms of action, tests against which microorganisms and test development phase
Experimental design: no comment
Validity of the findings: no comment
Additional comments: no comment


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

Input:
Title: ANTIMICROBIAL PEPTIDES PROPERTIES BEYOND GROWTH INHIBITION AND BACTERIAL KILLING
Review round: 1
Reviewer: 2

Output:
Basic reporting: This review is interesting. the authors show recent information about these antimicrobial peptides. the subject is of interest to the microbiological community. i have some minor comments.

in the section "Other anti-virulence targets of AMPs" I suggest adding headings on the topics type III secretion systems, bacterial toxins and other targets to facilitate the reader's better understanding of AMPs.

In the conclusions section, figure 2 is cited before figure 1, which is not  orthodox.

Other minor comments include :

53 type III, III means IV?

99 typo: delete ")"

100 typo: delete ")"

195 please define : EPS

197 for  the reader clarity, replace "calliphora vicina", for   from the insect calliphora vicina.

199 clarify "S. epidermis" is Streptococcus or Sthaphylococcus ?

200  please clarify for first time  is P. aeruginosa, Pseudomonas aeruginosa?

239 replace PA01 for Pseudomonas aureginosa PA01

245 the reference: "De la fuente and colleagues 2012", does not exist in the references

249 typo: burkhodetia

254-261 please cite these results

271 define CLS

315-316 please cite these results

366 is B. anthracis? Bacillus

392 define TC system

470 define FDA
Experimental design: no comment
Validity of the findings: no comment
Additional comments: no comment


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

Input:
Title: MEASURING MASS: VARIATION AMONG 3,161 SPECIES OF CANADIAN COLEOPTERA AND THE PROSPECTS OF A MASS REGISTRY FOR ALL INSECTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: In this study Hu et al. quantify the variation of body mass for more than 3,100 beetle species from Canada, employing the BIN approach based on DNA barcodes for their discrimination. In my eyes, the topic of this manuscript is interesting and appropriate for “PeerJ”, but I feel that some aspects should be pointed out/discussed more in detail.

The authors claim that “… factors such as the loss of an appendage, variation in humidity, specimen age, and curatorial practices have small impacts on these (mass) measurements.” I think it would be nice to provide some examples of a direct comparison of old and fresh specimens, at least for some selected abundant species. I do not see the necessity to rely for such studies on the existence of DNA barcodes for the analyzed specimens if the identification/classification is without doubt.

Furthermore, strong mass and size variations are well-known for numerous families and genera, e.g., the genera Pterostichus (Carabidae) or Otiorhynchus (Curculionidae), whereas other genera have almost no size/mass variation (e.g., Nothiophilus or Dyschirius (both Carabidae)). I feel that the authors should present some specific examples of their results.

Phenotypic plasticity is a well-known phenomenon for a variety of beetle species, e.g., for stag beetles (Lucanidae), and can affect mass and size of specimens significantly. A discussion of this aspect is still missing but should be added.

Finally, I feel that there is a good chance to increase the number of relevant references.

Please check the uploaded pdf for details also.
Experimental design: The research question is well explained, the used methods adequate. Many data, however, rely only on one analyzed specimen per species. What can you say about the intraspecific variation for the studied species with more than one specimen/species? I think these data are important to show.
Validity of the findings: As already pointed out I think that the topic of this manuscript is interesting and appropriate for “PeerJ”. However, I feel that the authors should present some specific examples of their results.
Additional comments: Maybe the authors can provide some images of pinned specimens and/or insect boxes for illustration.


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: MEASURING MASS: VARIATION AMONG 3,161 SPECIES OF CANADIAN COLEOPTERA AND THE PROSPECTS OF A MASS REGISTRY FOR ALL INSECTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: DNA barcoding reference libraries are critical to help species identification, especially for hyperdiverse taxa. However, vouchers associated metadata are often overlooked while they may be used and of importance in ecological studies. Linking biological traits like body mass to these reference libraries can be helpful to further use DNA (meta)barcoding in ecological and functional studies rather than biodiversity inventories only. In that sense, this paper is a real effort to improve associated DNA barcoding reference libraries metadata and a great contribution to the field overall. While the main pitfall is the huge number of singletons used to mass species proxy, the work remains of a great scale and has to be acknowledged. The work around curatorial categories is also of interest to standardize mass measurements from collection specimen.

In that sense, I believe that the article fits the scope of PeerJ, with a research being sound and of potential interest to a broad audience.

Main comment 1:
I have been a bit surprised to learn only L. 96 (in the Material and Methods) that the 3,161 species are actually 3,161 BINs. I fully agree and acknowledge the use of BINs as species proxy, but this should be clarified earlier (abstract and introduction) in the manuscript. Mentioning directly BINs as species proxy or genetic species under consideration would clarify the manuscript and remove doubt to the reader, as BINs are not always following Linnaean delineation. Indeed, you show L. 103 that your actual BINs with species level (2,719) correspond to 2,389 recognized species. This is 330 SPLIT cases that actually inflate your species count when considering BINs as species. Please clarify your manuscript accordingly, when using BINs as species proxy or recognized species (See secondary comments 1 and 3, but also title, abstract and all manuscript parts).

Main comment 2:
One issue I face in the manuscript is the huge number of singletons considered for weighting BINs (3,744 individuals for 3,161). I acknowledge the huge “sampling” effort it took to weight all these individuals to generate mass data. Actually, I believe that the number of individuals should be earlier mentioned in the manuscript (L. 23 in Abstract and 73. in Introduction) to better emphasized the impressive work here. However, I do lack more discussion on the intraspecific variability that can arise within species. Paragraph L. 220 – 229 nicely discuss interspecific mass variations, but nothing is said about the intraspecific variation. Considering that sex, resources availability, reproduction strategies, etc are important factors that can make interindividual mass vary greatly (potentially even greater than some interspecific variations), please acknowledge and discuss this shortfall and that further work should be done to complement the database in that sense.

Main comment 3:
You mention L. 111 that you had three main curatorial categories (ethanol, pointed, pinned). I was wondering if you had BINs with multiple curatorial categories available (through multiple individuals) to also compare between them directly?

Main comment 4:
Sentence L. 69–71 is important. I believe that the article would gain in importance if shortly discussing the implication of this work for such techniques (e.g. to help inferring relative abundance for example).
Experimental design: no comment
Validity of the findings: no comment
Additional comments: Secondary comment 1:
L. 87–88: Please nuance a bit the sentence as the BIN system clustering does not always correspond at 100% with Linnaean species.

Secondary comment 2:
L. 201: Please provide full T-test parameters (t = XX; df = XX; p-value = XX).

Secondary comment 3:
L. 212: If not clarified earlier in the manuscript that BINs are used as species proxy, please clarify “3,161 species of Coleoptera”. (See main comment 1.)

Comment on supplementary data availability and reproducibility:
I thank you for publishing the dataset with a proper DOI. However, I lack R scripts for the analyses performed. For the sake of reproducibility, could it be possible to make it available on GitHub or other public and dedicated repository, along with the data used (e.g. humidity, weights in 2014 and 2018, weight of appendage, etc), with a link or DOI mentioned in the appropriate section of the manuscript?


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

Input:
Title: EFFECTIVENESS OF INTERACTIVE TEACHING INTERVENTION ON MEDICAL STUDENTS’ KNOWLEDGE AND ATTITUDES TOWARD STEM CELLS, THEIR THERAPEUTIC USES, AND POTENTIAL RESEARCH APPLICATIONS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors have carried out in interesting study, where they have attempted to evaluate a teaching module on Stem Cells, with pre- and post- course surveys. Together with the surveys, the course design and the ethical approval, I expect this would have been a significant amount of work. The approach of making the effort to collate and publish such data should be commended.

Generally the standard of writing is good. There are some parts than need clarification (see below).

The meanings of the following sections are unclear and should be redrafted:
Line 192 'dully' should be 'duly'
Line 310 - what does 'as a spread' mean?
Line 329 - 'carry and excellent deal'

The following comments could be considered minor:
Abstract background: Line 61 change to...with the potential to alleviate many non-treatable...This avoids the double us of  'treat'.
Line 62: Drop 'The' in 'The medical students...'.
Line 65: Add 'an' to ...effectiveness of (an) interactive
Line 115: Maybe replace 'groundbreaking' with 'novel' or 'pioneering'?

The paper is also formated with the correct sections.

In the other section below I have commented about providing additional references.

Raw data: The additional data is provided as an SAV file. It does not appear that this is one of the recommended journal file formats. SAV appears to be a proprietary SSPS file, but it cannot be opened by other data analysis programs (without add ons). The editorial team should comment on whether this file format is acceptable, however this reviewer cannot examine the raw data in the format provided.
Experimental design: Ethics:
The supplementary documents provided have confirmed alignment to the Declaration of Helsinki.
Participants were all consented and a copy of the consent form in included in the supplementary documents
The consent forms and the paper state that the surveys were anonymous. However, the survey included the student names (line 151- 153). The names were needed to allow the paired t-test, however, this implies that the data collection appears to be inconsistent with the participant consent form. This issue and should be resolved before publication.

Data analysis:

The survey question appears to contain true and false statements. However, this should be mentioned specifically in text: this reviewer has had to infer that from the true/false statements in table 3 (also note that the true/false statements are not explained in the table). There appears to be 10 true statements and 6 false statements (the authors do not provide a numerical breakdown).

In table 3 and the discussion text, it appears that students improve in their agreement with true questions (by more firmly agreeing with the statement and so the score increases) after the training. However, the students also agree stronger with the false questions (by more firmly agreeing with the false statement and so the score increases when it should decrease). This appears to happen in all the false questions (although the reviewer has had to infer this because it is not discussed in the paper). This issue should be addressed before publication.

Line 234-235: two scores 1.84 (SD = 0.63) to 2.45 (SD 0,80) have a p value < 0.001? It's a paired t-test but this does seem like a very low probability. Can the authors confirm this result?.
Validity of the findings: Results and discussion comments:

Line 207 - 'media' be 'social media', as the survey form stated the latter
Line 208 - Data is not presented, but the authors should confirm that the information is in the dataset (see the previous raw data comment).
Line 235-238: Could this sentence be clarified: it’s not clear if the values are referring to the understanding of side-effects, or the understanding of tumor formation potential?

Line 277: The text states that the participant's knowledge is not sufficient in the pre-intervention phases, however by what criteria or standard was this statement made. What defines 'insufficient knowledge'?
Line 283: the authors have attempted to show that an interactive educational approach in SC has benefits to medical students. However, (and with the caveats stated in other paragraphs), the paper doesn't show that the educational approach had to be interactive, or that because it was interactive it was better than a didactic class. The paper should clarify this issue.
Line 285-6: some justification (perhaps a reference) of the statement that an education SC module would improve the overall health service is needed.

Line 303-304: Can the authors state at the end of this sentence what other studies they are referring to, and provide and analysis to demonstrate that this SC module was more 'comprehensive, detailed, and engaging' than those other studies. This question does not appear to be part of the survey.

Line 312- As above, the term media is used, whereas the survey question was related to social media, this should be clarified. The discussion then moves onto 'mass media', which maybe different than social media. Kamenova and Caulfield looked at newspapers (according to their abstract), and so the text should clarify this.
Line 317 - 321: Some evidense (perhaps a reference) is needed for the claim that panel discussions are a 'valuable way to trigger an exchange of viewpoints'.
Line 324 - what are all the knowledge domains? Is it the Basic Knowledge, Potential Applications, Therapeutic Uses and Research? The term 'Knowledge domains' in the educational context could refer to the Cognitive, Affective and Psycho-motor domains of Bloom's hierarchy of learning. Can this be clarified in the text.

Line 334 - Pourebrahim et al. 2020 seemed to conclude that in Iran, SC research and applications should be restricted. This appears to contradict the authors statement in line 338.
Line 366 - Looking at table 5 the gender differences have not vanished, they are still there, but are not statistically significant (perhaps using 'statistically insignificant' may be a suitable term?)
Line 367-369: no evidence is presented that the interactive method of teaching was interesting or that the students were more enthusiastic about a course designed with this approach. There is no data to support the experience of researchers.
Additional comments: As with all reviews, I have tried to take a detailed look at the dataset, analysis and conclusions. I recognised that in some cases my points may be brought on by uncertainity in the text, or my understanding, or a combination of both. I do hope the above issues can be addressed and that with revision this paper could be published.


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: EFFECTIVENESS OF INTERACTIVE TEACHING INTERVENTION ON MEDICAL STUDENTS’ KNOWLEDGE AND ATTITUDES TOWARD STEM CELLS, THEIR THERAPEUTIC USES, AND POTENTIAL RESEARCH APPLICATIONS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The authors elaborated the need for their study, the methodology of their course and questionnaire, and the pre vs. post-intervention student outcomes clearly. There are minor errors in English language. For example, the terms "stem cells (SCs)" when combined with a noun such as "biology" or "education" should be replaced with the more appropriate singular of  "stem cell." Overall, however, there are no major grammatical errors. The provided tables are well-designed, clearly reflect survey results, and are easy to read.
Experimental design: The authors clearly defined their goal of gauging both attitude and knowledge about stem cell science in medical students before and after a targeted, six-session course. They provided adequate information about ethics, enrollment in the study, demographics, and how metrics were assessed, with the survey being included for our review. The curriculum is elaborated both in prose and in Table 1.
Validity of the findings: The metrics of mean score pre vs. post-intervention seemed appropriate, with the majority of these scores being evaluated with a paired T-test to determine significance. One area where the data analysis may be reconsidered is in table 3, questions 5-13. These true-false questions could be reported in a binary, true/false percentage rather than a sliding scale, which would be a more meaningful metric to assess competency. The authors should also comment more on scores that were relatively low or high in magnitude, even if they improved after intervention.  Another discussion that would be relevant to the scope of the article is specialty-related competencies--which fields of medicine were encompassed by the curriculum?
Additional comments: Overall, this appears to be a well-designed curriculum and study. As SC usage becomes more common across specialties, having clinical curriculum that educates future physicians on SCs is increasingly important. To be of interest to a large readership, the most important findings from this study might be a discussion of any shortcomings or gaps (rather than just successes), so that educators at other institutions can capitalize on opportunities to improve areas of their own stem cell curricula.


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: GENOME-WIDE IDENTIFICATION AND EXPRESSION ANALYSIS OF THE VQ GENE FAMILY IN CUCURBITA PEPO L.
Review round: 1
Reviewer: 1

Output:
Basic reporting: The use of English language, grammar and phrasing of sentences is quite satisfactory. The paper was easy to comprehend and had a clear flow to it.  The authors do a good job of introducing the properties of C. pepo L that make it valuable as well as the importance of studying the VQ gene in plant stress regulation.
Experimental design: The study was conducted quite thoroughly especially in documenting the gene expression changes and molecular responses against various stress factors like drought, powdery mildew, cold, salt on Cucurbita pepo L. The data seems backed by various statistical analysis which makes the findings realistic and reliable.

The authors show extensive use of bioinformatics tools and techniques as well as provide specific versions of each tool used which would help in reproducibility of the results.
Validity of the findings: The study seems to be a first of its kind to throw light on VQ and its role in protecting Cucurbita pepo L under abiotic stresses. What is actually interesting to note that the unsupervised clustering of CpVQs under powdery mildew stress is able to classify each of the genes into their specific phylogenetically classified group.
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: GENOME-WIDE IDENTIFICATION AND EXPRESSION ANALYSIS OF THE VQ GENE FAMILY IN CUCURBITA PEPO L.
Review round: 1
Reviewer: 2

Output:
Basic reporting: Authors should provide relevant references they are missing throughout the manuscript. Please provide relevant references for the statements, one such example is Line 37-40. Another example is Line 45-47 "In Arabidopsis… plants".

Line 70-71 "widely .. Worldwide", "in" should be dropped. Authors should do a thorough proof-reading of the manuscript and use unambiguous English language for the international readers to follow.

Line 132 Title "VQ gene…" formatting is not consistent, there are several instances where the manuscript formatting is not up to the journal standards. Please use consistent formatting across the entire manuscript.
Experimental design: Methods described in the manuscript are relatively clear, but authors should address the below concerns for improvements.

Line 92 authors should provide full forms of Abbreviations Example: "CDD"

Line 99 "multiple sequence aliment" should be multiple sequence alignment, please correct similar mistakes across the manuscript.

Line 103-104 “The phylogenetic tree was edit and illustrate by iTOL (http://itol.embl.de/help.cgi) online tool”. Please correct the English language and rephrase.
Validity of the findings: Lines 84-92, “HMM profiles of the VQ motif (PF05678)…. (E-value) cut-off was set as 0.1 (Punta et. al, 2012). The Arabidopsis Information Resource (TAIR) database (http://arabidopsis.org) was used as queries to conduct a local BLASTP against the protein database of Cucurbita peop. The targeting genes with similarity of E-value less than 1e-20 were retained for the further analysis".  Authors, please elaborate on why different e-values were used?

Line 167-168 Authors should explain what do they mean by "After manually removing redundant entries through screening and validation of the search results". What screening criteria and validation were done before deleting certain entries?

Line 183 Authors mentioned VQ proteins were divided into 8 groups, they should elaborate on how these 8 groups were identified?

Line 281-288 "Construction …… conditions" This result section is not clearly written, and the description of Figure 12 is vague. Currently in my opinion it is not adding any value to this manuscript. Please rewrite and provide context for the readers.
Additional comments: This study investigated the VQ genes in the C. pepo L. genome and analyzed their phylogeny. In addition to this expression level of CpVQs was analyzed under abiotic and biotic stresses. The manuscript is not easy to follow. Please thoroughly proof-read the manuscript and use unambiguous and professional English. Overall, the manuscript requires major revision and clarifications before acceptance. I have included my comments in the various section along with some general comments below.

1) Introduction needs improvement and should be rewritten to provide sufficient background to determine the significance of this work. Currently, it's hard for the reader to follow as there is no connection or flow from one statement to another.

2) Similar research work is conducted on VQ genes in 2016,2019( https://doi.org/10.3389/fpls.2015.01177, Doi: 10.7717/peerj.7509). Authors should comment and discuss how this manuscript adds to what is already known in the field.

3) Genome-wide identification and expression analysis of the VQ gene family have been carried out in many plant species as referenced above. The authors should make relevant comparisons among published VQs and their identified VQs.

4) Authors should discuss the difference in expression trend for VQ Group 3 compared to all other groups (as observed in Fig. 6)? Why group 3 has upregulated expression later in time after powdery mildew stress?

5) Line 297-299 Authors should clarify what they mean by "deeper analysis and investigations" What kind of analysis will this study support? Please provide specific details.

6) Line 355-363 "In this study …..Therefore, the members of the VQ family in C. pepo L. play a key role in the powdery mildew signaling pathway." It is not evident from this paragraph how the authors came to this conclusion? Authors should reframe or provide additional evidence supporting this statement.


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: GENOME-WIDE IDENTIFICATION AND EXPRESSION ANALYSIS OF THE VQ GENE FAMILY IN CUCURBITA PEPO L.
Review round: 1
Reviewer: 3

Output:
Basic reporting: The manuscript is very poorly written. Some of the details is given below.
Experimental design: The authors have not mentioned the nature of replicates.
Actin for RT control has been used from other plant sps.
Detail is given below in additional comments.
Validity of the findings: Biological replicates should be added in RT PCR validation.
Incomplete short sequences should be completed by amplification and sequencing or TSA/EST/Nr blast, if available in the database.
Additional comments: The Ms entitled ‘Genome-wide identification and expression analysis of the VQ gene family in Cucurbita pepo L.’ is very poorly written. It should be revised thoroughly for grammatical and technical errors..
1.	Correct the name of crop as ‘Cucurbita pepo’ in the entire manuscript. It is written C. peop at many places.
2.	Write down the botanical name of plants in the entire manuscript and italicize them.
3.	Articles missing at many places. Include ‘The’ before the name of Kits and Tools used in the Ms.
4.	When CpVQs are written in context to protein, they should not be italic. Only gene name will be italicized.
5.	Lot of grammatical errors have been done in the manuscript. So, here is a need of deep revision of every line.
6.	Firstly, write down the full forms with abbreviation in bracket like molecular weight (MW), then only abbreviation should be used in the entire manuscript. Same can be used for other words.
7.	Figure 2 and 3 are not clearly visible.
8.	The results and discussion part should be elaborated.
Abstract:
1.	Line 17 should be rewritten.
Introduction:
1.	Lines 64 to 65 found confusing. It should be rephrased.
Materials and Methods:
1.	In Line no. 109, CpVQs should not be italicized.
2.	The reference cited in line no. 131 not found to be relevant with respective line.
3.	Treatment was in biological or technical replicates, explain properly.
4.	TBTOLLS citation is missing. Even link is not given.
5.	Why C. moschata actin is used as internal control? Why not from the same plant gene?
6.	I could not see any statistical analysis for RT data.
Results:
1.	In line no. 170, the gene length and length of coding sequence are the characteristics of gene, not protein. It should be corrected.
2.	Why there is much variation in the length of proteins? It might be incomplete sequence. Try to complete the length by TSA blast or amplification and sequencing of short genes.
3.	In line no.180, the VQ should not be italicized as here it represents the family name, not gene.
4.	In line no. 182, VQ genes should be replaced with VQ proteins.
5.	The line no. 189-190, don’t found to be relevant. It should be rephrased.
6.	Line no. 193-194, the function of gene cannot be determined from gene structure studies (number of exons and introns). So, this line should be corrected.
7.	Line no. 207-208, does not make any sense. So, it should be rephrased.
8.	In line 211, the heading should be replaced as “chromosome mapping and duplication events analysis”.
9.	Line  212 doesn’t find to be relevant. Therefore, it should be replaced.
10.	Mention the gene distributions on chromosome 6.
11.		Line   220, “BLSTAP” should be replaced with “BLASTp”.
12.		Line  237 is confusing. It should be rewritten.
13.	The results regarding “Expression pattern of the CpVQs under powdery mildew stress” were concisely written. Therefore, these results should be elaborated.
14.		Line  254-255 should be corrected because CpVQ36 gene exhibit upregulation at 0 h of stress treatment, which indicate that it might be involve in early response.
15.	Line no. 255 and 256, should be corrected, because the genes CpVQ1, CpVQ12, CpVQ14, CpVQ26, CpVQ33, CpVQ34, and CpVQ40 are not significantly increased as displayed in figure 8.
16.	Line no. 260-261 should be corrected. The reported genes in your manuscript are not found to be significantly upregulated at early hours of stress as shown in the Figure 9.
17.	Line no. 271-272, should be mentioned clearly.
18.	Line no.282-283 should be corrected.
19.	The results of expression analysis have been written concisely. Therefore, the results should be elaborated and written with more clarity.
Discussion:
1.	Discussion should be elaborated. Most of results has not been discussed.
2.	Author should discuss the number of VQ genes in other plants also, so that the comparative idea will be available for their distribution in various plants. Why higher number of VQ genes in C. pepo than other dicot plants? What is relation of ploidy level and genome size with the number of VQ gene in various plants?
3.	The line no.309-310 should be rewritten. Discuss the phylogenetic relationships with more points and in clear manner.
4.	Line no. 319-321 is not clear. It should be rephrased.
5.	Line 368-369 should be grammatically corrected.

Figure quality is very poor. Some figures are not visible properly such as figures 2,3 7-11, etc.
Figure legends should also be elaborated.
Why expression analysis is done in only stress treatment not in any tissue developmental stages?


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: GENOME-WIDE IDENTIFICATION AND EXPRESSION ANALYSIS OF THE VQ GENE FAMILY IN CUCURBITA PEPO L.
Review round: 2
Reviewer: 1

Output:
Basic reporting: There are still some minor grammatical errors in the manuscripts that need to be addressed.
Experimental design: Experimental design is good enough after modification done by authors as pointed in my previous report.
Validity of the findings: Additional clarifications as requested by reviewers are now supplied and Irrelevant information such as Fig12 is removed. The introduction is sufficiently clear after being re-written.
Additional comments: Overall, the authors have satisfactorily addressed all of the reviewer’s concerns.


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: GENOME-WIDE IDENTIFICATION AND EXPRESSION ANALYSIS OF THE VQ GENE FAMILY IN CUCURBITA PEPO L.
Review round: 2
Reviewer: 2

Output:
Basic reporting: The Ms still needs improvement.
Experimental design: In RT-PCR, earlier they have written actin gene as internal control, now they are writing CAC gene. Either it was negligence of author, or they have wrongly mentioned about the control gene.
What is this CAC gene? why it has been used as control? is there any evidence of homeotic expression of this gene? Is it a gold standard for expression analysis? I don't think so. In that case, authors should use more than one internal control, which has been regular practice now a day.
Validity of the findings: Authors did not seems to be consistent at there own reports.
Additional comments: Manuscript is still very poorly written. Even, they have still not correctly written the name of his studies plant at all the places. For instance at line 213, C.peop  is written in place of C. pepo. If they can not write the correct name of the studied plant, then how one can expect better Ms from them.
Even in title, despite of suggestion to italicize the gene name, it is still not done. Is VQ not the gene name in title?
Authors have highlighted all the Ms, in place of highlighting the changes, how one can see the actual changes from the earlier Ms?


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: GENOME-WIDE IDENTIFICATION AND EXPRESSION ANALYSIS OF THE VQ GENE FAMILY IN CUCURBITA PEPO L.
Review round: 3
Reviewer: 1

Output:
Basic reporting: Grammatical errors were addressed
Experimental design: Experimental design is good enough after modification done by authors as pointed in my previous report.
Validity of the findings: Additional clarifications as requested by reviewers are now supplied
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: GENETIC DIVERSITY OF INDIGENOUS GUINEA FOWL (NUMIDA MELEAGRIS) USING MICROSATELLITE MARKERS IN NORTHERN TOGO
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: Abstract
Line 27: ‘Indigenous guinea fowl are an important’. Please change ‘are’ to ‘is’.
Line 28: Please change ‘incomes’ to ‘income’.
Line 30: Please indicate the two agroecological zones.
Line 31: Why the use of 18 markers only? I thought the standard recommended by FAO is 25 and above. How were the 94 individuals sampled?
Line 38: How can you justify this assertion ‘three probable parental populations’?
Line 40: Please reconstruct the sentence.

Introduction
Line 51: Be cautious with the use of ‘is’ and ‘are’ in describing guinea fowl. If you are referring to a particular type or breed, use ‘is’. However, if you are making reference to more than one type or breed, use ‘are’.
Line 57-59: What about the use of mtDNA for maternal relationship?

Materials and Methods
Line 77-87: Kindly provide more information such as existing population of birds in the two zones, the vegetation and predominant agricultural activities and tribes.
Line 91-92: Why the difference in the number of samples for each zone?
Line 96: is this correct ‘International Center Research and Development on Livestock in Subhumid zone)?
Line 98: What standard range values did you use for this ‘purity and concentration’?
Line 102: Why only 18 markers?
Line 119: What did you use to view the bands before sequencing?
Line 134-135: You should have compared you NJ tree with that of maximum likelihood or maximum parsimony.

Results
Line 166: Change ‘Excepted from ‘ With the exception of’
NB: The result section is very good.

Discussion
Line 198: The study should have been complemented with mtDNA for a balanced report.
Line 201: Put a comma after’ (5/18)’
Line 208-211: Please try and discuss your findings before comparisons.
Line 235: What about birds in the wild? How have they influenced this diversity?
Lines 253 and 264: Why repeating the figures which have already been presented under ‘RESULTS’?

Conclusion
Line 273: Please rephrase.
Line 274: Please check

References
The references are adequate, but no consistency in the formatting.


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: GENETIC DIVERSITY OF INDIGENOUS GUINEA FOWL (NUMIDA MELEAGRIS) USING MICROSATELLITE MARKERS IN NORTHERN TOGO
Review round: 1
Reviewer: 2

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Numida meleagris represents an important source of income for families living from agriculture in Africa. In the Introduction section, the authors begin justifying the study by the economic importance of the species in agriculture and also by the lack of information about the species' indigenous populations in Togo. Previous studies on genetic diversity based on analysis of mitochondrial DNA and microsatellite markers (Kayang et al. 2010; Botchway et al. 2013) revealed the absence of genetic structure in domesticated populations of Numida meleagris, indicating a recent domestication and rapid dispersal by Africa. Therefore, the study in natural populations is important because it represents a source of variability for the genetic improvement of the species. Although the aim of the authors is to assess the genetic diversity and structure of populations in northeastern Togo, they do not specify how the results will contribute to the management and improvement of conservation and management techniques. This gap stems from the lack of a hypothesis to be tested. In my view it could not be formulated since the authors do not report what is already genetically known about the domestication of the indigenous populations. The introduction lacks information. I suggest reading Vignal et al. (2019) that, although using a different molecular tool, the SNPs, draws a rich panorama regarding the domestication of the species in different regions of Africa. According to Vignal et al. (2019) there is an absence of genetic structure among domestic populations, however, there is divergence between these and native populations.

Another aspect that can only be noticed when reading the methodology is that the authors want to verify the possible relationship between genetic structuring and plumage color. In the introduction there is no mention of the mode of inheritance already defined by Ghigi (1924, 1966) for the guinea fowl. Different modes of inheritance, autosomal dominant or incomplete dominance, are involved and again the lack of basic genetic information on the subject makes it impossible to formulate a hypothesis to be tested regarding a possible correspondence between genetic structuring and plumage color.

Regarding the results, the number of base pairs of the amplicons of each locus should preferably be informed in Table 1. The compliance with the Hardy-Weinberg equilibrium should be tested for each locus and the results showed.

The authors said that increasing the sample number per phenotype concludes that it is necessary to include a greater number of individuals to be able to attribute their origin. One thing, in my view, is the data obtained with the sample number used to suggest an assignment. Another is that there is no attribution suggestion with the used markers. What is the sample number sufficient to make the analyzes robust? This evaluation must be prior to the study, establishing at least the minimum necessary sample size.

Lines 258-260, the authors conclude “In addition, the microsatellite markers used in the present study are neutral markers and therefore, are not involved in the determinism of the expression of feather coloring genes”. Therefore, if they had gone a little further into the introduction and included this already well-known evolutionary property of microsatellite markers, they could have predicted what would happen at the end of the study. For this purpose, some candidate gene locus, most notably EDNRB2 (Vignal et al. 2019), seem to be more appropriate. But the authors apparently contradict each other when on line 269 they consider that: “Increasing the sample size per phenotype would no doubt lead to more robust conclusions”. I mean, should the sample number or molecular marker be revised?

Regarding the replication of the methods, there is no reference to the DNA extraction method. The acronym mentioned is cited in the Thesis by Romé (2015) but also without a description of the methodology and was not found in another reference.

Still regarding the representation of the results, all of them are not self-explanatory. It is not informed which results are presented, regarding which species, from which location(s). On the map, for example, there is only the region of Togo, without locating it in Africa. In Weimann et al. (2016) is a good example, where the authors include the African continent in the image and highlight the studied location. For example: “Map of Togo in Africa with the locations of the X populations of guinea fowl genetically, Numida melagris. Authors just sated in the legend: Figure 1. Sampled sites locations. Of what, where, what was sampled? Figure 3 Agroecological zones – in the figure Atakora and “Dry” there is no mention of the region, the objective of the analysis, figure 5 there is no mention to the colors of the STRUCTURE diagram. All subtitles must be rewritten.

Of minor concern

Lines 271/273 change "structuration" to "structuring"

In citation of two authors change “and” to “&”

In references, adapt as the instructions to authors, eg, journal name in italics, no indent from second line onwards, remove the period from some references, no dot in authors' initials.


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: GENETIC DIVERSITY OF INDIGENOUS GUINEA FOWL (NUMIDA MELEAGRIS) USING MICROSATELLITE MARKERS IN NORTHERN TOGO
Review round: 2
Reviewer: 1

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: no comment
Additional comments: no comment


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

Input:
Title: GENETIC DIVERSITY OF INDIGENOUS GUINEA FOWL (NUMIDA MELEAGRIS) USING MICROSATELLITE MARKERS IN NORTHERN TOGO
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors were carefully dedicated to observing the suggestions submitted and were clear about the aspects that cannot be answered due to the prioritized experimental design. With the modifications made, the manuscript is better structured. Starting with the most consistent introduction, in terms of the presentation of the state of the art regarding studies in Numida meleagridis, relevant to the focus of the manuscript, for example, the objectives were defined, the mode of inheritance of plumage coloration was informed, the extraction methodology of the DNA, the size data of the amplified alleles.

Importantly, the inclusion made by the authors regarding the fact that plumage color can be an indicative aspect of genetic structuring. Therefore, the theme is more robust based on the bibliographical references added.
Experimental design: It still needs correction in Methods:
L. 153 It consists of "extracting" DNA from....
L. 155 After incubation.... 250 uL of saturated NaCl (usually cold) was added per sample.
Keep correcting all the description of the DNA extraction method using past tense to match the rest of the described methodology, once it has already been executed.
L. 173 rephrase the sentence. "reactions (PCR) was carried our using."

The data about Hardy-Weinberga expectations and the size of amplified alleles were also included.

L338-342 - It was important that the authors included a future perspective and the need for additional studies regarding the EDNRB2 gene as a likely candidate to investigate the occurrence of various phenotypes in domesticated populations.
Validity of the findings: No comment.
Additional comments: No more 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: GALAPAGOS LAND IGUANAS AS ECOSYSTEM ENGINEERS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The writing is generally clear, but some sentences area a little convoluted and long.  For example:
- ln 42: "a process envisioned with contemporary ecological theory built around interaction networks" - this phrase is likely not needed.
- ln 43-46: This sentence is too long. Why is it difficult to estimate the "magnitude of effect of one species on the distributions and abundances of others"?

Literature references are generally good, but there were a few spots where a connection to the literature could have been improved.
- ln 62: "impacts of reptiles on vegetation are essentially unknown."  There is a wealth of knowledge on the impacts of the other large reptilian herbivore in the Galapagos, giant tortoises.  There are many papers that could be cited, including those by the authors and highlighted in their recent book.  In addition, there are many papers on effects of Aldabran tortoises and other large tortoises around the world on plant communities.  This phrase should be removed.
- ln 71: The citation to Merlin & Juvik 1992 is about a quasi-experiment with introduced herbivores.  I would appreciate seeing an example (or justification) of a quasi-experiment with naturally occurring herbivores that may have been present for long periods of time (see my concern about the study design and inference below).  The Beatty et al. citation does not seem to be about quasi-experiments with herbivores.

I appreciate the sharing of the raw data, but it could use a metadata description of what the column headers mean.
Experimental design: It is not clear to me why there is a focus on "rewilding" in the title and introduction of the paper.  There is not any translocation being conducted in the study, it is more about the ecosystem impacts of herbivores.  There are implications for the practice of rewilding, but since the herbivore was not manipulated (i.e. removed or introduced) it is a bit of a weak connection.  I would suggest only bringing up rewilding in the discussion as it is an implication of the study (i.e., if iguanas have a large effect on their ecosystems, then there is an argument to be made that they need to be reintroduced to the ecosystems they once inhabited).  With this in mind, it would also be helpful to know where land iguanas are currently distributed compared to where they were in the past.  It is not clear from the introduction that land iguanas are even in need of reintroduction.  Given statements such as "land iguanas often dominate as the only large-bodied herbivore present" (line 76) - this seems to indicate that they are present everywhere that they should be, and thus not in need of reintroduction.  (Also, what about giant tortoises as large-bodied herbivores?)

It would be good to see some hypotheses/predictions in the introduction about what you expected to find.  There are some hints at this (e.g., line 81, where there is a discussion of iguana effect on cactus reproductive mode), but this could be made clearer as a specific prediction.

Methods:
There is a good description of the two islands, but there are two key differences about the islands that are not mentioned, both of which could potentially affect the plant community.  South Plaza Island is a tourist site with high visitation rates; whereas North Plaza is prohibited from visitation.  Although tourists are instructed to stay on trails, there is inevitably some wandering (and thus trampling) that could influence the vegetation.  South Plaza Island also has a substantially steeper slope than North Plaza, which can influence water flow/infiltration and thus what plants are present.  These differences need to be described as they could both have impacts on plant community composition.
Analysis:
It is not clear what the "experimental unit" is in the Bayesian ANOVAs to estimate the effect of treatment.  (It is also not clear why this is a Bayesian analysis, when a standard ANOVA would seem to be suitable for a one factor analysis.)  Arguably, there is a single replicate for each treatment (each island is a replicate, as the authors acknowledge in the discussion), but that is clearly not the approach taken in the analysis as statistics could not be estimated with a single replicate.  It seems from the results that each 5x5m grid cell is likely taken to be an experimental unit, resulting in the extremely high and extremely low values in Table 1.  I don't think it's appropriate to consider each grid cell to be an independent unit - there is a lot of spatial autocorrelation in vegetation cover, and some of these individual plants may cover more than one 5x5m cell.  I see 2 options: 1) remove the Bayesian ANOVA analysis and simply report the %cover differences and nMDS analysis which are convincing enough of the differences between the islands, or 2) account for spatial autocorrelation in the statistical analysis.  There are potentially multiple ways to do this, an easy thing to do would be to subsample the pixels at each island to reduce the chances that a sampled 5x5m cell is near another sampled cell.

Table 1: More description of what the Bayes Factors mean would be helpful, as this is not a common analysis.  What does a large BF10 indicate?  Is there a threshold for interpretation?
Validity of the findings: The results are fairly clear in terms of the vegetation differences between the two islands.  My concern is with the interpretation that these differences are entirely due to the effect of iguanas on the plant community, when it is entirely possible that the differences simply indicate what is habitat for the species.  In any other system, if researchers described the plant community of where an animal is present and where it is absent, we would infer that the plant community characteristics of where it is present are descriptive of the species' habitat.  The difference here is that this is an island system, and so the assumption is that iguanas cannot get to North Plaza.  However, both of these islands are very close to the larger island of Santa Cruz and they are very close to each other.  It seems very likely that, over evolutionary time, land iguanas would have gotten to North Plaza multiple times, and so the question is, why are they not there now?  One potential explanation is that the conditions do not provide suitable habitat - perhaps woody plant density is too high, or grass cover too low.  The authors argue that iguanas created the opposite conditions on South Plaza, but the converse could be equally true (that iguanas are only present because the conditions on South Plaza favor their presence).  Without a true experiment, it is impossible to say whether the iguanas are present because of the habitat or that the iguanas are causing the plant community to be structured as it is.  The authors need to at least discuss this possibility.  It would be helpful if there was some discussion of the habitats that the species is found in throughout the archipelago.

Line 191: The sentence ends by stating that iguanas are targeting "woody plant regeneration" with their herbivory, but then the next sentence goes on to discuss cladodes, which I assume is referring to the cactus.  There is no evidence provided that iguanas eat woody plants - either adults or saplings.

Generally, the discussion was a little superficial and did not delve into the results.  Many questions remain unaddressed.
- There were substantially more marine mammal impacts on South Plaza (iguanas present) - could this be due to differences in topography?  Could marine mammals be having an influence on the plant community in the rest of the island?  The authors indicate that marine mammals deposit large amounts of guano (nitrogen) - how could this influence plants on the island?
- What would the mechanism be for how iguanas would promote grasses over woody plants?  Giant tortoises might do this through trampling, but it is hard to see how iguanas would have the same impact.
- Please discuss more the potential impacts of the introduced mice.  There is some thinking that the mice had a large impact on the regeneration of cactus (through eating seeds) - how might this play into the dispersion pattern that was reported on?
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: GALAPAGOS LAND IGUANAS AS ECOSYSTEM ENGINEERS
Review round: 1
Reviewer: 2

Output:
Basic reporting: In terms of basic reporting, the language is pitched at the right level, the manuscript is well-paced and well-structured, and the language is clear. The context is sufficient, except for the issues I have raised below. The figures are presented in a professional manner. The raw data has been shared and is well-described. The study is self-contained and the results are directly related to the hypothesis.

Comments on figures:
Figure 1 caption: Does the colour of the grid cell indicate the dominant vegetation type, i.e. the one with the highest proportion? If so then the caption should explicitly state this
Figure 2: The caption does not include a description of the top right panel which, in the text is referred to as “2b”.
Figure 2: The data provided with the manuscript has a precision of 10% for vegetation cover. This could be more faithfully represented graphically by using histograms with 11 bins. The kernel density estimates in Figure 2 imply higher resolution than the original data and, if used, require justification.

Comments on citations:
The citations do not clearly support the claims in several places
Lines 43-46: The claim that the effects of herbivory are difficult to predict is puzzling and this claim is a little vague. I suggest simply claiming that there is good evidence that biotic factors influence distribution and abundance (e.g. Wisz et al) and that herbivores often act in several ways to structure vegetation communities (e.g. Maron and Crone 2006) but that effects depend on the particulars of ecosystems.
Line 51: I suggest instead finding evidence of increasing numbers of rewilding projects, or cite similar claims by authorities (e.g. Svenning et al. 2016)
Lines 55-56: Islands are arguably not a major focus of rewilding, given the number of projects in mainland Europe. It would make more sense if the authors claimed that islands should be a major focus of herbivore rewilding for ecosystem recovery—a claim that is their own and needs no citation—and then continue with the very reasonable justification of that claim in the sentences that follow.
Line 69: The description of the study as a ‘quasi-experiment’ should be linked to Shadish et al 2002 rather than Allen et al 2017.

Typographic and grammatical errors:
Line 34: author order is incorrect
Line 35: suggest “…especially for tropical islands from which they have been extirpated…”
Line 53: suggest “…in the absence of herbivory”
Line 63: There is no need for quotation marks around the word ‘rewilding’
Line 83: suggest “…is intense”
Line 86: suggest ‘…iguanas, we contrasted’
Line 98: suggest ‘…Plaza islands”
Lines 105: suggest ‘…Plaza islands”
Line 121: suggest “…imagery”
Lines 133: suggest “…identify individual”
Lines 134: suggest “…delineate the extent”
Line 137: suggest “…cell made up by the following”
Line 143: suggest “…counted the number”

Maron, John L., and Elizabeth Crone. "Herbivory: effects on plant abundance, distribution and population growth." Proceedings of the Royal Society B: Biological Sciences 273.1601 (2006): 2575-2584.
Svenning, Jens-Christian, et al. "Science for a wilder Anthropocene: Synthesis and future directions for trophic rewilding research." Proceedings of the National Academy of Sciences 113.4 (2016): 898-906.
Wisz, Mary Susanne, et al. "The role of biotic interactions in shaping distributions and realised assemblages of species: implications for species distribution modelling." Biological reviews 88.1 (2013): 15-30.
Experimental design: The research is original, and within the scope of the journal. The investigation appears rigorous and the methods are, for the most part, described in full.

Comments on methods:
Line 151: I am not familiar with Bayesian ANOVA, so my comment may be overly cautious: The authors should show that the transformed data adequately meets the assumptions of Bayesian ANOVA. Certainly this would be the case for frequentist ANOVA (and even with an arcsin tranformation, in the latter case, the data would likely not meet those assumptions given the high proportion of cells with value “0”). Alternatively, the authors might consider a logit transformation and generalised linear regression (Warton and Hui 2011).

Lines 159: I did not understand why confidence intervals were generated. It was implied that the authors counted every cactus in every 5x5m grid cell, in which case they have the population mean and variance for the number of cactus per cell for each island. If the CIs were generated for some other reason, perhaps it should be stated.

Warton, David I., and Francis KC Hui. "The arcsine is asinine: the analysis of proportions in ecology." Ecology 92.1 (2011): 3-10.
Validity of the findings: The authors should more explicitly address the competing hypotheses for the underlying causes of differences in vegetation between the islands (see lines 87-89). To convince the reader that iguana feeding behaviour is the most likely cause of vegetation differences then the authors need to also convince the reader that the other plausible explanations are less likely. They can do this by giving more detailed evidence about
- the likelihood of lasting impacts of house mice
- the likelihood of lasting impacts of goats (e.g. see Campbell and Donlan 2005)
- differences between the island soils, topography and weather
- the effect of vegetation on sea lion basking sites and vice versa (to rule out the effect of sea lions on vegetation) (i.e. lines 202-204), if any observations have been published.
This extra information will make the claims better justified and make an already-interesting study more so.

The tone of the title, abstract and discussion promises somewhat more than the evidence delivers. Arguably, the authors did not 'demonstrate' (line 183) that large-bodied, herbivorous reptiles can substantially engineer the structure of terrestrial plant communities. They did, on the other hand, provide good evidence for that hypothesis. I suggest re-wording the claim to better reflect the limitations of the study.

Comments on results:
Line 170: do the authors mean “surrounded by more woody plants cells” rather than “surrounded by more woody plants”?
Lines 176-177: regarding the phrase “areas dominated by grasses only and marine mammal impacts only were unique to the island with iguanas present whereas areas dominated solely by woody plants were unique to the island lacking iguanas”, this should be re-stated for clarity. There are grass-dominated areas on both islands, for example (Figure 1). I suggest “cells with 100% woody plant cover” etc.

Minor comments on discussion:
Line 224-5: since this study is not about a recovering ecosystem, I suggest rewording this phrase to highlight instead the potential for restoring important ecosystem
Line 227: suggest “we provide some evidence that land iguanas substantially engineer …”
Line 232:  suggest “restoration in systems where they have been extirpated”

Campbell, Karl, and C. Josh Donlan. "Feral goat eradications on islands." Conservation biology 19.5 (2005): 1362-1374.
Additional comments: Congratulations on taking advantage of a neat natural experiment and applying non-invasive methods to describe a striking comparison. It may have important implications for the trophic ecology and the restoration of island ecosystems.

Overall, I felt that the paper was well balanced and the methods and results were well described. However, the strength of the evidence for the hypothesis that iguana herbivory is the primary cause of vegetative difference is somewhat overstated in places. This is not to say that the results are not valuable and worth reporting—they are—but more a cautious conclusion and more evidence against competing conclusions will make the manuscript both more robust and more interesting.


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: GALAPAGOS LAND IGUANAS AS ECOSYSTEM ENGINEERS
Review round: 1
Reviewer: 3

Output:
Basic reporting: The present study aims to analyse the ecosystem-scale impacts of Galapagos land iguana (Conolophus subcristatus) on structuring plant communities. For this, authors compare plant communities (by using high-resolution maps) in two adjacent (and comparative) islands with/without iguanas to assess the role of this large-bodied herbivorous species on vegetation. They found that in presence of iguanas there was 208% less woody plant cover, 52% more area
with grasses, and 258% less cactus.

The topic of this MS is really interesting. However, some aspects of the MS (see below) need to be considered in order to improve it. My principal concern is related to the presence of goats (and house mice) in the island with Conolophus (South Plaza island). Thus, since iguanas and goats coincide recently in the past in this island, the role of goats on vegetation in South Island need to be discuss in more detail. Besides, instead these islands are very near each other and its expected similar levels of e.g. precipitation, I am wondering about other environmental factors which can affect vegetation cover instead presence of iguanas. I mean, e.g. soil/rock cover, soil type, soil nutrients, vegetation impact of human near in the past, presence of seabirds and others (because presence of guano), etc. These aspects need to be included in some way to know the real effects of iguanas on vegetation cover. Besides, the role of iguana such as herbivorous vs. seed dispersers need to be analysed in more detail. What about data of iguana’s diet in this specific island? Could authors also used historical aerial photos of these islands in those years with goats and house mice were eradicated? Could Opuntia species also being negatively affected by other biological factor instead Conolophus, e.g. some Coccoidea species?
Experimental design: no comment
Validity of the findings: no comment
Additional comments: No additional comments


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

Input:
Title: GALAPAGOS LAND IGUANAS AS ECOSYSTEM ENGINEERS
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No Comment
Validity of the findings: No comment
Additional comments: The authors have done a good job responding to my comments and those of the other reviewers.  I think that the paper is now ready for publication and will represent a meaningful contribution to the literature on reptile ecosystem engineering.


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: GALAPAGOS LAND IGUANAS AS ECOSYSTEM ENGINEERS
Review round: 2
Reviewer: 2

Output:
Basic reporting: Line 43: there seems to be some confusion around the Cook et al reference. The version I can see online is here: https://www.alnap.org/system/files/content/resource/files/main/147.pdf, which has the author order as Shadish, Cook, Campbell. Google Scholar has the author order “TD Cook, DT Campbell, W Shadish”. I’ll leave it to the copy editor to make a call on that one.
Line 45: suggest change ‘a’ to ‘an’
Line 145: suggest change ‘cactus considerably’ to ‘cactus was considerably’
Lines 207-208: The authors might consider that iguanas may have also colonised the island but lost the small population lottery
Line 226: ‘substantially’ is a repeated word
Line 226: ‘that, the’: suggest remove comma
Figure 2: the top right sub-figure does not match the description. Other parts of figure 2 are violin plots but this is a line plot. It is not clear from the caption why this figure differs from the others, and what it represents. In the text at lines 141-2 it is described thus: “Correlation of woody cover extent in each 142 5 x 5 m grid cell and extent of woody vegetation in the eight neighbouring grid cells (Fig. 2b)” but the subfigure itself is not marked ‘b’. I suggest marking the individual sub-figures and making the description explicit.
Experimental design: No comments
Validity of the findings: This version is argued in a more balanced and convincing way.
Lines 155, 162. If the evidence is ‘strong’ then the authors can do more than merely ‘suspect’ the effects were due to iguanas. I suggest ‘the evidence gives us good reason to believe that the dramatic effects… etc etc.’
Additional comments: I’m looking forward to seeing this in print.


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: GALAPAGOS LAND IGUANAS AS ECOSYSTEM ENGINEERS
Review round: 2
Reviewer: 3

Output:
Basic reporting: In this revised version the MS has been improved in relation to comments of previous reviewers. The topic (the impact of herbivores on insular vegetation) is really interesting. However, some questions (and doubts) to formulate that vegetation changes among these island can be entirely due to the effect of land iguanas are not well resolved yet. Below I have included some comments to be considered in this revised version:

L39.- Maybe authors can include other general references about reptiles such as herbivore and seed dispersers (instead only tortoises) to include herbivore (Cooper & Vitt 2002, J Zool), and seed disperser (Valido & Olesen 2019, Frontiers Ecol Evol) lizards, as wells.

L40.- Other examples about consequences of reptile declines on insular vegetation are the next: Perez-Mendez et al. 2016 (Sci Reports), Perez-Mendez et al. 2018 (J Ecol).

L52.- Include latin names of three species of Galapago land iguanas

L77. Mat & Methods. I also miss a detailed description of climate and soil conditions in both islands. These aspects can also affect vegetation cover and composition

L93.- Include “vertebrate fauna”

L155.- Since South Island include in some way feral goats, tourist, mice, sea lions, instead Conolophus, authors need to discuss in detail their specific impact on vegetation. I mean, can these factors affect the observed differences on vegetation cover, presence of grasses, and density of Opuntia? These aspects (such as alternative hypotheses) need to discuss in more detail at time to use the sentence “This study provide strong evidence…” I’ll see that previous reviewers asking this point too, but evidences about in the MS is not really convincing yet.

L193.- Relate to previous point (L331) related to presence of goats and mice, authors need to discuss in more detail this sentence “but are unlikely to account for the striking differences in plant communities evident today”. It is not clear that between island differences can be entirely due to the effect of land iguanas.

L198-201.- To support this conclusion, it would be interesting to see these data on Results, as wells.

In general the Discussion need to be re-written according to other potential factors influencing vegetation changes and showing clear evidences that they are less likely to compared with consequences of land iguanas.
Experimental design: 'no comment'
Validity of the findings: 'not comment'
Additional comments: 'not 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: SHOULD I USE FIXED EFFECTS OR RANDOM EFFECTS WHEN I HAVE FEWER THAN FIVE LEVELS OF A GROUPING FACTOR IN A MIXED-EFFECTS MODEL?
Review round: 1
Reviewer: 1

Output:
Basic reporting: Generally clear and complete throughout.
Experimental design: No comment (see general comments below)
Validity of the findings: Overall this paper makes a good point: I completely agree that it is unwise to thoughtlessly omit a blocking factor from a statistical model if there are 'insufficient' levels. While respecting that a single paper can't do everything, and that one has to start somewhere, I was concerned about the lack of broader theoretical discussion, and the very specific set of simulations on which the results are based.
Additional comments: SCOPE

I am exceedingly nervous about basing general advice on a single set of simulations that can be considered a special case in many ways: (1) a linear mixed model (rather than a GLMM, for example); (2) a balanced design (the values of the numeric covariates X1 and X2 differ across sites, but the number of observations per site, and the range of X1 and X2, is balanced/identical across sites; (3) particular choices for the relative magnitudes of residual and among-group variability, and for the magnitude of the fixed effects relative to the variability (signal-to-noise ratio); (4) evaluating across-site variation only in the intercept (no variation in the slopes either in the simulated data or in the model). I am particularly nervous because of the finding that dropping the random effect [pseudoreplication] doesn't influence the probability of type-1 errors, and the results that show that the rate of rejection of the null hypothesis is independent of subsample size in the real-data case study ... if I got these results, which seem to contradict what would be expected from theory, I would work hard to try to figure out what was special about my setup that drove these counterintuitive results: are the rates of rejection in fact changing in the expected direction, but by a very small magnitude? Is there something about the choice of experimental design and parameters that makes this case unusual, or can these results be reliably generalized to the broad range of ecological data analyses? (For example, Bates et al (2015) criticize Barr et al (2013) for simulations that use unrealistically large effect size, casting doubt on their conclusions.)

COMMON PRACTICE

The author asserts in several place that ecologists drop random effects entirely from the model when they deem that there are insufficiently many levels of the grouping variable (l. 118 "[t]he current state of practice in ecology is to drop the random effects terms"; also l. 333 "typically drop random effects"). Given that it's *not* would I would advise (I would typically say to treat the effect as fixed rather than random, cf l. 192), I'd very much like to know the foundation for the claim: is this actually *recommended* anywhere? Is there a systematic review that evaluates the commonness of the practice? In the (likely) absence of either of these (or other) pieces of evidence, it would be good to qualify this statement by saying that it's the author's observation ... (It would also be good to know if there is published advice explicitly recommending substitution of fixed effects for random ...) (Now I see that there is a potential list of papers supporting this contention on ll. 377-378, and countervailing practice on ll. 379-381; it might be good to foreground this comparison, and perhaps do a slightly more systematic comparison [an analysis of a sample of, say, 50 recent papers from ecology, stating number of levels of the grouping variable and the strategy followed, doesn't sound like an unreasonable amount of work, and would be extremely valuable].

METRICS

The author evaluates bias, finding that the results are effectively unbiased, and type-I error. Bias is OK (it has some odd properties of varying with measurement scale - for example, an unbiased estimator for the variance will be biased for the standard deviation), although I would be more interested in relative root mean squared error (i.e. sqrt(mean((beta_est/beta_true-1)^2))) (I suspect it will still be tiny.) I would strongly encourage the author to evaluate _coverage probability_ (computationally, 90% coverage probability will be easier to evaluate to a given level of precision than 95% coverage, although readers may be more comfortable with 95% coverage). Coverage probability has two major advantages of (1) being equally applicable to zero and non-zero effects and (2) getting away from the morass of what exactly one is doing when evaluating type-1 errors. For example, line 129 needs to be read carefully: if "one does not exist" is read as "when the effect is exactly zero in reality", it's correct, but it's easy to misconstrue as "detect a significant effect when the effect is not significant [but not non-zero]", which is nonsense but superficially plausible. Switching to analyzing coverage, one could also eliminate most of the slightly distracting paragraph after l. 349 that discusses issues with p-values, generally and in mixed models particularly. Finally, type-1 errors *only exist* in simulations, where one can set an effect to exactly zero (ecological effects are practically never zero), but coverage (an estimate of the reliability of estimates of uncertainty) is applicable both in simulations and in the real world. (As long as one is going to compute estimates and confidence intervals for each run, there is little computational cost to evaluating bias, variance, RMSE, and coverage ...)

I might not bother evaluate the estimates of the intercepts (which are rarely of scientific interest) and instead evaluate the scaled RMSE and coverage for a range of slopes.

TERMINOLOGY

Unfortunately the terminology associated with REs is often vague; the difference between the complete random-effect term (e.g. "correlated random intercepts and slopes associated with variation across sites"), the grouping variable associated with that term (e.g. "sites"), the levels of the grouping variables ("site 1, 2, 3 ..."), and the BLUPs/conditional modes determining the predicted deviations of an effect strength [intercept, slope, etc.] in each group from the population mean ("site 1 slope effect = -1.2"), are all sometimes called "random effects".

l. 14: "random effect" = "grouping variable"; "five levels of the grouping variable associated with a random effect" might be more precise.

l. 77 "random effect" = "conditional mode/BLUP"

  fixed effect (conservative)
  Bayesian (more challenging)
  leave alone (overestimate?)

What is suggested for singular models?

Matuschek et al "balancing"

MINOR COMMENTS
====

l. 50-51: occupancy, N-mixture, mark-recapture models don't really belong (IMO) to the class of GLMMs: most of them require a more general form of latent variable than GLMMs can accomodate. (They are "hierarchical" or "latent-variable" models, but not GLMMs ...)

l. 56: I would call binomial, Poisson, etc. a "response distribution" or a "conditional distribution" rather than a "data generating process"

l. 57-58 the "sampling distribution" refers to the distribution of an estimated coefficient across realizations, not to the conditional distribution of a response variable.

l. 58 not sure what "mean-centered" means here. Even more picky, technically a Gaussian would be most appropriate for a *real-valued* response (i.e. one where negative values would be realistic); non-negative or positive values as given in the examples would better use a Gamma or log-Normal (or other transformed-Normal) response distribution. That said, if the coefficient of variation is small, then modeling these variables as Gaussian is standard.

l. 65 why are "average temperature" and "sound pressure levels" italicized?

l. 66 "other" variables are often referred to as "nuisance" variables in statistical contexts (this is used below on l. 116; if it were defined here one wouldn't need quotation marks later)

l. 79 "This": unclear antecedent

l. 97 I might say something about "documented" or "systematic"; there's presumably a lot of _anecdotal_ empirical evidence developed by the authors quoted ... even if some are merely copying assertions from previous authors ...

l. 107 why emphasize "most cases" when "many cases" is sufficient (and Kéry and Royle already say "vast majority")?

l. 124 "this": unclear antecedent

Figure 2 caption "The bias in sigma starts to approach the starting (simulated) sigma=0.5" should "bias approaches zero" or "mean estimated value approaches the true value"?)

eq 2.1 it is more common to include the overall intercept (mu) as a constant in the equation for the response, and make the site-level effects explicitly zero-centered (i.e. Normal(0,sigma)) (I prefer a centered dot (2·b), juxtaposition (2b), or perhaps an x (2×b), for multiplication, rather than *, in mathematical equations)

l. 207 "latter of which" (awkward)

l. 214 I would expect that a binomial confidence interval (e.g. Clopper-Pearson, although the Normal approximation should be OK with p~0.05 and 10000 samples) derived from the number of samples (10,000) and the observed probability would be fine - bootstrapping seems overkill.

l. 248, 256 "resurrect" doesn't seem quite right; "reconstruct"?

l. 253 "lead" → "led" or "eads"

l. 256 "non-important" → "unimportant"

l. 281 "probability of"

l. 337 "higher probability of significant p-values" → higher probability of rejecting the null hypothesis at alpha=0.05

===
Barr, Dale J., Roger Levy, Christoph Scheepers, and Harry J. Tily. “Random Effects Structure for Confirmatory Hypothesis Testing: Keep It Maximal.” Journal of Memory and Language 68, no. 3 (April 2013): 255–78. https://doi.org/10.1016/j.jml.2012.11.001.

Bates, Douglas, Reinhold Kliegl, Shravan Vasishth, and Harald Baayen. “Parsimonious Mixed Models.” ArXiv:1506.04967 [Stat], June 16, 2015. http://arxiv.org/abs/1506.04967.

Matuschek, Hannes, Reinhold Kliegl, Shravan Vasishth, Harald Baayen, and Douglas Bates. “Balancing Type I Error and Power in Linear Mixed Models.” Journal of Memory and Language 94 (June 1, 2017): 305–15. https://doi.org/10.1016/j.jml.2017.01.001.


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: SHOULD I USE FIXED EFFECTS OR RANDOM EFFECTS WHEN I HAVE FEWER THAN FIVE LEVELS OF A GROUPING FACTOR IN A MIXED-EFFECTS MODEL?
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper is mostly well written. Only a few minor changes are suggested below.

On the literature, see Clark & Linzer 2015 (this paper should probably be discussed in the intro and discussion as it is quite similar).

Clark, T., & Linzer, D. (2015). "Should I Use Fixed or Random Effects?" Political Science Research and Methods, 3(2), 399-408. doi:10.1017/psrm.2014.32)
Experimental design: This paper addresses an interesting topic in statistical ecology using both a simulation study and case study. Overall, the experimental design is good.

L 262-264: Consider using REML to get more accurate variance estimates.
Validity of the findings: The premise of this article was not clear until line 196 and many statements make it unclear throughout. It sounds as if they were going to drop the effect of site rather than include it as a fixed effect. In several places, it talks about dropping (L 118-120, L333), ignoring (L 207-208), missing (L 365) or omitting (L 369) the random effect which is not exactly the case in the LMs. The abstract even says that the LMs commit pseudoreplication (L22-24) but this is false because they include a fixed effect of site. When the literature says that fewer than 5 levels of a random effect are too few, the alternative is to account for it using a fixed effect as was done here.
Additional comments: Results of simulations should state how often variance was estimated as zero (to some precision) or non-convergence warnings/errors were produced as these are some of the reasons that people suggest > 5 levels of a random effect.

L 18: "terms" should be "levels"

L43: The citation for glmmTMB should be
> citation("glmmTMB")

To cite glmmTMB in publications use:

  Mollie E. Brooks, Kasper Kristensen, Koen J. van Benthem, Arni
  Magnusson, Casper W. Berg, Anders Nielsen, Hans J. Skaug, Martin
  Maechler and Benjamin M. Bolker (2017). glmmTMB Balances Speed and
  Flexibility Among Packages for Zero-inflated Generalized Linear Mixed
  Modeling. The R Journal, 9(2), 378-400.

A BibTeX entry for LaTeX users is

  @Article{,
    author = {Mollie E. Brooks and Kasper Kristensen and Koen J. {van Benthem} and Arni Magnusson and Casper W. Berg and Anders Nielsen and Hans J. Skaug and Martin Maechler and Benjamin M. Bolker},
    title = {{glmmTMB} Balances Speed and Flexibility Among Packages for Zero-inflated Generalized Linear Mixed Modeling},
    year = {2017},
    journal = {The R Journal},
    url = {https://journal.r-project.org/archive/2017/RJ-2017-066/index.html},
    pages = {378--400},
    volume = {9},
    number = {2},
  }

L45: missing comma after "biologists"

L48-51: Kéry has changed the way he refers to site-ocupancy and N-mixture models since his book which equated them with GLMMs; now he calls them "non-GLMM hierarchical models" because they're slightly different from GLMMs. This text needs to be changed accordingly.

L57: Warton 2005 found that negative binomial is usually good for abundance data, so it would be better than Poisson when you reference wildlife counts.

Warton, D.I. (2005), "Many zeros does not mean zero inflation: comparing the goodness-of-fit of parametric models to multivariate abundance data". Environmetrics, 16: 275-289. https://doi.org/10.1002/env.702

L 68-70: I don't think this sentence is necessary and could draw criticism because it only applies to GLMMs in an MLE framework, but not a Bayesian one.

L 79 and elsewhere: "group" should probably be "level of the random effect" or "blocks" or make a statement that you're using it this way throughout because the meaning could be anything in line 84. This is sort of done on line 96, but could be earlier and more direct. In the methods section around line 148, this changes to "site" for a site-level intercept.

L 224: Give original data set size before resampling scheme.

L 368 and throughthout "repeat-measures" sounds odd to me. Isn't it usually "repeated-measures".