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: HOST DIETARY SPECIALIZATION AND NEUTRAL ASSEMBLY SHAPE GUT BACTERIAL COMMUNITIES OF WILD DRAGONFLIES
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors claim that the data is deposited within the European Nucleotide Archive under the accessions: PRJEB32318, PRJEB32316, PRJEB32311, PRJEB32309, PRJEB32308. I am unable to access theses in order to determine if these data are compliant with MIMARKS standards (and am thus unable to determine if all associated meta data, analyzed within this manuscript, is provided for reproducibility of the work). I refer the authors to the following:

Yilmaz, Pelin, Renzo Kottmann, Dawn Field, Rob Knight, James R. Cole, Linda Amaral-Zettler, Jack A. Gilbert, et al. 2011. “Minimum Information about a Marker Gene Sequence (MIMARKS) and Minimum Information about Any (x) Sequence (MIxS) Specifications.” Nature Biotechnology 29 (5): 415–20.

Permits for field work appear to have been obtained from Shendurney Wildlife Sanctuary: permit no. WL 10-3781/2012 dated 18/12/2012, and GO (RT) No. 376/2012/F and WLD dated 26/07/2012). I have no way of confirming if these are appropriate permits. Additionally, it does not appear if permits were either required or obtained from the other sampling cites: Agumbe Rainforest Research Station, Bangalore, Nagpur, Bordubi.

Line 234: State here all of the specific R packages used. I realize some are listed later, but the specific commands / parameters used are quite vague on some places.

Line 236-237: What tool was used to perform rarefaction analyses? QIIME? An R package like Phyloseq or mctoolsr? It may behoove the authors to provide a simple ordered set of commands / flowchart detailing the analysis pipeline.

Lines 273-287: This seems like quite a robust approach! When describing the parameters, it’d be useful to show or reference the formula(s) in which these parameters are entered. Although the authors reference the R script from Burns et al, it is unclear which tables were used as input, i.e. what was considered the actual meta-community. Given the large amount of detail provided in other areas of this manuscript and within supplemental information, I am not sure why the authors chose not to also share their code / pseudo code / notebooks via github or other means too? I do not think I would be able to reproduce these steps.
Experimental design: Lines 110, 120, 127: To be clear separate individuals were used for each of these steps? That is, those used for FISH / qPCR (b) are different than those used for microbiome analysis (a)? If so, please explicitly state this.

Line 101 – 104: If I understand correctly, sampling was repeated from October through January at each location? How many times, please provide dates / time points. Otherwise, it is not clear how the assessment of community assembly can be performed without reference to a temporal component. Please clarify.

Line 120-123: I am a little confused by the statement referring to the 4-6 hours that the dragonflies were allowed to defecate and clear their guts. If that is all that is needed to remove most of the fecal material, then how can the later statement, that fecal material may represent a 3-5 day snapshot of diet be true?

Line 170: To be clear, the data set totals 45 dragonflies, or 45 dragonflies per species? IF the former, how many per species?

Lines 169-175 / 193-194: The authors assume that readers will understand why Hasora sp. is a “control”.  This will not be clear to those not familiar with these molecular surveys. The authors should explicitly explain why this phytophagus taxon is being used as a control. They should also bring up the problems associated with potentially amplifying and sequencing host DNA, particularly when using the COX1 gene, and cite the appropriate literature. They also need to make note of what proportion of reads were from the host, versus food/prey items. I’d expect a box-whisker plot of how many reads are from the host compared to the total reads. The Kaunisto paper does reference the amount of host sequences obtained, which is quite substantial (71-84% are from host; Figure 1). I am concerned that the authors did not look into constructing a blocking primer or peptide nucleic acid clamp (PNA) to inhibit sequencing host DNA. These methods have been around for quite a while (especially for COX1) and the authors should state why this host-blocking approach was not implemented or not needed. Much of the recent advancement in limiting host amplification and sequencing to assess diet has been largely ignored by the authors within this manuscript. The authors should be referring, at the very least, to several of the following seminal papers in this field:
1)	Vestheim, Hege, and Simon N. Jarman. 2008. “Blocking Primers to Enhance PCR Amplification of Rare Sequences in Mixed Samples – a Case Study on Prey DNA in Antarctic Krill Stomachs.” Frontiers in Zoology 5 (1): 12–11.
2)	Deagle, Bruce E., Simon N. Jarman, Eric Coissac, François Pompanon, and Pierre Taberlet. 2014. “DNA Metabarcoding and the Cytochrome c Oxidase Subunit I Marker: Not a Perfect Match.” Biology Letters 10 (9): 20140562–20140562.
3)	De Barba, M., C. Miquel, F. Boyer, C. Mercier, D. Rioux, E. Coissac, and P. Taberlet. 2014. “DNA Metabarcoding Multiplexing and Validation of Data Accuracy for Diet Assessment: Application to Omnivorous Diet.” Molecular Ecology Resources 14 (2): 306–23.
4)	Kartzinel, Tyler R., Patricia A. Chen, Tyler C. Coverdale, David L. Erickson, W. John Kress, Maria L. Kuzmina, Daniel I. Rubenstein, Wei Wang, and Robert M. Pringle. 2015. “DNA Metabarcoding Illuminates Dietary Niche Partitioning by African Large Herbivores.” Proceedings of the National Academy of Sciences of the United States of America 112 (26): 8019–24.
5)	Lundberg, Derek S., Scott Yourstone, Piotr Mieczkowski, Corbin D. Jones, and Jeffery L. Dangl. 2013. “Practical Innovations for High-Throughput Amplicon Sequencing.” Nature Methods 10 (10): 999–1002.
6)	Piñol, J., V. San Andrés, E. L. Clare, G. Mir, and W. O. C. Symondson. 2014. “A Pragmatic Approach to the Analysis of Diets of Generalist Predators: The Use of next-Generation Sequencing with No Blocking Probes.” Molecular Ecology Resources. https://doi.org/10.1111/1755-0998.12156.
7)	Brandon-Mong, G-J, H-M Gan, K-W Sing, P-S Lee, P-E Lim, and J-J Wilson. 2015. “DNA Metabarcoding of Insects and Allies: An Evaluation of Primers and Pipelines.” Bulletin of Entomological Research 105 (6): 717–27.
Note, I am not criticizing the use of COX1 or lack of blocking primers/probes, only that the authors should bring up known limitations using these approaches, then discuss whether or not they think these limitations may or may not affect the authors overall interpretations. I suspect likely not.

Lines 205-207: I think the authors are confusing de novo, open-reference, and closed-reference OTU-picking. It appears they only made use of the open and closed reference approaches. Although de novo is a component of open-reference, the wording of this sentence makes the reader assume three methods are being compared. I am generally fine with any of these approaches, however, there is strong potential for the count inflation of some OTUs using these approaches. Or, more to the point, the dropping of reads that to not “hit” the database, not necessarily because they are not within the database, but the stopping criteria is met before an actual “hit” is found. I hope the authors adjusted the `max_accepts` and `max_rejects` flags of the open and close reference approaches by setting them to larger values or setting them both to `0` (exhaustive search). Though this is more of an issue for the closed-reference approach. By this, I mean that the authors may not be aware of how usearch / uclust actually works. I highly recommend reading this online blog post by Scott Olesen entitled “What you think usearch does might not be what it does.”
http://scottolesen.com/post/what-you-think-usearch-does-might-not-be-what-it-does/
Again, I am not dissuading the use of closed reference approaches, but they authors should be aware and point out the parameter settings used, as well as the caveats associated with these settings. There is literature on the subject, but I simply felt the blog post is a more “fun” way to learn about this. Finally, the authors need to make sure they cite all of the tools used that are contained within QIIME and/or the R packages. For example, the authors do not cite uclust or the open /closed reference approach:
1)	Edgar, Robert C. 2010. “Search and Clustering Orders of Magnitude Faster than BLAST.” Bioinformatics  26 (19): 2460–61.
2)	He, Yan, J. Gregory Caporaso, Xiao-Tao Jiang, Hua-Fang Sheng, Susan M. Huse, Jai Ram Rideout, Robert C. Edgar, et al. 2015. “Stability of Operational Taxonomic Units: An Important but Neglected Property for Analyzing Microbial Diversity.” Microbiome 3 (1): 20.

Lines 214-217: The easy-to-access / download files from the Barcode of life is not very complete. In fact there is much more information that can be accessed via the R package “bold”, where this data should be downloaded (if not done so already). Even better, I highly recommend that the authors use the reference database constructed by Teresita Porter:
1)	https://github.com/terrimporter/CO1Classifier
2)	Porter, Teresita M., and Mehrdad Hajibabaei. 2018. “Automated High Throughput Animal CO1 Metabarcode Classification.” Scientific Reports 8 (1): 4226.
3)	Porter, Teresita M., and Mehrdad Hajibabaei. 2018. “Over 2.5 Million COI Sequences in GenBank and Growing.” Edited by Wolfgang Arthofer. PloS One 13 (9): e0200177.

Line 410: Clarify how many individuals per dragonfly species were sequenced. This sentence is ambiguous, do you mean 5 individual hosts or 5 individual host species? If only 5 hosts, then I am concerned that this is not a large enough sample size to make robust inferences. Probably a good idea to perform a power analyses using micropower to determine effect size in future studies.
Validity of the findings: Line 217-221: I agree with the authors that removal of Odonate sequences may hide any dietary / ecological insight related to conspecific predation. I thank the authors for making this really good point! Again, although clear to me, many others may not understand the issue of obtaining a large amount of sequence from the host. This must be explicitly stated in the manuscript. However, it’d be nice to simply know the percentage of general Odonate sequences obtained that do not specifically classify to the host sample. They could conjecture that this “might be” a signal of conspecific predation. Actually, the authors could use this to address my earlier comment about blocking primers, in part. That is, blocking primers (i.e. Vestheim) will likely block the conspecific predation signal. But if they are not concerned with this issue (or it is too difficult to discern given the particular amplicon region chosen to access diet), then a blocking primer should be considered / discussed. However, if they are interested in blocking host DNA, then this would only argue for the use of PNA, which can be tailored to be species-specific as they are far less “leaky” (i.e. blocking other off-targets) than blocking primers.

Line 609-611: What dates were these sites sampled? I am concerned that temporal variability in diet may conflate “partitioning out” the effects of the role of geography and diet. Can more information be provided on the prevalence of diet items within each region? Do they fit with the diet items found via COX1? Temporal variation in food item availability has a large impact on feeding behavior / diet.

Lines 58-61: This is over generalized. Even generalists will focus on a “favorite” or preferred  food item as the season change. See the literature related to pigs, for example. I’d assume the same is potentially true for some insects too. I think the authors should cite other references, that specifically discuss these topics. The references used here to not appear to make any claims, nor do the studies seem to be explicitly designed to address ecological community assembly processes of the gut microbiota, e.g. stochastic assembly. Furthermore, any stochasticity observed in these studies is conflated, in large part, by the fact that the (greatly summarized by the cited Yun paper) “…insect gut as a bacterial habitat shows different morphologies, generally depending on the insect order; furthermore, the gut morphology is sharply changed by metamorphosis, according to the life cycle of the insect. Additionally, the oxygen availability can be influenced by gut shape, metabolism of colonizing bacteria, and partial pressure of oxygen from the outside environment, and the pH, from acidic to extremely alkaline conditions, is determined by different gut compartments in diverse insect individuals. These diverse gut conditions may cause the variation in host-specific gut microbiota in insects.”

Lines 80-82: I think the authors should more clearly define what they mean by “generalist predators” as this term can be ambiguous, and often considered a redundant term. Do the authors simply mean generalist in the sense of, eating many different species? For example, a predator can feed on many different species (generalist in reference to species), but limited by the size of the prey species, or even the nutrient composition of the prey species. So, in this sense, the predators can be considered specialists, e.g. eating only prey items they can handle within a certain size range. Also, they may be generalists in what they consume throughout the year but, they prey upon items that are abundantly available in a given season (i.e. seasonal specificity), or the nutrients the prey items provide. Predators typically have more plasticity compared to their herbivorous counterparts. Again, even generalists will focus on a “favorite” or preferred food item when present. I refer the authors reader to:
1)	Unsicker SB, Oswald A, Köhler G, Weisser WW. Complementarity effects through dietary mixing enhance the performance of a generalist insect herbivore. Oecologia. 2008;156(2):313–324. doi:10.1007/s00442-008-0973-6
2)	Jaworski CC, Bompard A, Genies L, Amiens-Desneux E, Desneux N (2013) Preference and Prey Switching in a Generalist Predator Attacking Local and Invasive Alien Pests. PLOS ONE 8(12): e82231. https://doi.org/10.1371/journal.pone.0082231

Lines 297-300: The authors are making an assumption that functional redundancy only exists among phylogenetically related taxa. This is not always the case. There is a decent amount of literature on the topic:
1)	Louca, Stilianos, Martin F. Polz, Florent Mazel, Michaeline B. N. Albright, Julie A. Huber, Mary I. O’Connor, Martin Ackermann, et al. 2018. “Function and Functional Redundancy in Microbial Systems.” Nature Ecology & Evolution 2 (6): 936–43.
2)	Koppel, Nitzan, Vayu Maini Rekdal, and Emily P. Balskus. 2017. “Chemical Transformation of Xenobiotics by the Human Gut Microbiota.” Science 356 (6344). https://doi.org/10.1126/science.aag2770.

Lines 378-381: Given the range of sequencing depth for the samples used as presented on line 205 (8k-900k) and 214 (29k-115k), even in non-rarefaction approaches the read depth shouldn’t not deviate excessively. That is: “Alternate normalization measures are potentially vulnerable to artifacts due to library size.” (Ref 3 below).  There are quite a lot of issues with non-rarefaction approaches if not performed or investigated properly. One of the factors, I suggest the authors read the following for more details:
1)	Weiss, Sophie J., Zhenjiang Xu, Amnon Amir, Shyamal Peddada, Kyle Bittinger, Antonio Gonzalez, Catherine Lozupone, et al. 2015. “Effects of Library Size Variance, Sparsity, and Compositionality on the Analysis of Microbiome Data.” e1408. PeerJ PrePrints. https://doi.org/10.7287/peerj.preprints.1157v1.
2)	Weiss, Sophie, Will Van Treuren, Catherine Lozupone, Karoline Faust, Jonathan Friedman, Ye Deng, Li Charlie Xia, et al. 2016. “Correlation Detection Strategies in Microbial Data Sets Vary Widely in Sensitivity and Precision.” The ISME Journal 10 (7): 1669–81.
3)	Weiss, Sophie, Zhenjiang Zech Xu, Shyamal Peddada, Amnon Amir, Kyle Bittinger, Antonio Gonzalez, Catherine Lozupone, et al. 2017. “Normalization and Microbial Differential Abundance Strategies Depend upon Data Characteristics.” Microbiome 5 (1): 59.
Additionally, the approach referenced by the authors may not perform well when considering that their data may be zero-inflated. Even when using variance / log-like transformations the signal of the original sequencing depth can still be present within the data and may affect downstream analyses. One great example of this is referred to below in Nieves-Ramirex et al. (be sure to also check the accompanied supplementary information / data). In fact, the Nieves-Ramírez paper used the approaches outlined in the references above. Thus, any analyses based on non-rarefied data need to be vetted. Which can also be an issue for differential abundance analyses (i.e. potential false positives). Again, these issues are outlined in the references above. Why was DESeq2 used over the plethora of other differential abundance tools? I’d recommend making use of DATest (Ref 2 below), to guide the most appropriate differential abundance based approach given your data (e.g. does your data fit a negative binomial approach, zero-inflated,… etc?).
1)	Nieves-Ramírez, M. E., O. Partida-Rodríguez, I. Laforest-Lapointe, L. A. Reynolds, E. M. Brown, A. Valdez-Salazar, P. Morán-Silva, et al. 2018. “Asymptomatic Intestinal Colonization with Protist Blastocystis Is Strongly Associated with Distinct Microbiome Ecological Patterns.” mSystems 3 (3).
2)	Russel, Jakob, Jonathan Thorsen, Asker D. Brejnrod, Hans Bisgaard, Søren J. Sørensen, and Mette Burmolle. 2018. “DAtest: A Framework for Choosing Differential Abundance or Expression Method.” bioRxiv, 241802.
Additional comments: The manuscript entitled “Host dietary specialization and neutral assembly shape gut bacterial communities of wild dragonflies” by Deb et al., attempts to determine the factors that may affect the composition of microbiota among several species of dragonflies. These factors included, host identity, geographic location, and diet. The authors made use of a variety of methods to parse out these effects, including the use neutral models of community assembly.

I have some concerns with the overall interpretations of the results given the very limited sample size of the study. The fact that this study was not planned as a longitudinal study is problematic for many of the authors interpretations. The authors do own up to this towards the end of this manuscript. Was the data from Nair & Agashe 2016 used for this study too? The authors used the approach of Burns  et al. 2016 for the assessment of community assembly. However, unlike Burns et al 2016 (and their own prior work) I was unable to follow how many time points where used for this study. Being that the authors focus much of their work on community assembly, I am surprised more clear details were not provided on how many time points they sampled. I plot similar to Figure 2 of Burns et al 2016 would be ideal.

The authors clearly did their due diligence with the FISH probes, alongside the assessment of microbial community and diet analyses… appears well thought out. The amount of work provided by the authors is quite substantial! I hope that, my somewhat long review, will help refine this already compelling piece of work.

Line 31-33: Clarify. Is this referring to the gut microbiome in general, or only those microbes that are ‘attached’ to the gut lining?

Line 34: The authors should state their overall results with explicit reference to their study system, and not generalize. Rephrase the sentence: “Our results contradict the expectation that host-imposed selection shapes gut microbiota, and highlight the importance of joint analyses of diet and gut microbiota of natural host populations.” To: “Our results contradict the more general expectation that host-imposed selection shapes gut microbiota of dragonflies, and highlight the importance of joint analyses of diet and gut microbiota of natural host populations.”

Lines 56-58: This is a very general statement. Provide at least one or two in-text examples of how dietary specialists continually promote these things.

Lines 183-187: When listing the primer sequences used, be courteous to your readers, please insert spaces or hyphens between the components of the primers, i.e. adapters, actual primer sequence, etc…

Lines 224-231: I really like this approach!

Lines 247-248: The authors bring up non-rarefaction approaches later in the manuscript, why not use such an approach for beta-diversity analyses too, such as Aitchison PCA:
1)	Martino, Cameron, James T. Morton, Clarisse A. Marotz, Luke R. Thompson, Anupriya Tripathi, Rob Knight, and Karsten Zengler. 2019. “A Novel Sparse Compositional Technique Reveals Microbial Perturbations.” mSystems 4 (1): e00016–00019.

Also, the authors should cite the original developers of the Canonical Analysis of Principal Coordinates based on Discriminant Analysis method:
1)	Anderson, M. J., and T. J. Willis. 2003. “Canonical Analysis of Principal Coordinates: A Useful Method of Constrained Ordination for Ecology.” Ecology. https://esajournals.onlinelibrary.wiley.com/doi/abs/10.1890/0012-9658(2003)084%5B0511:CAOPCA%5D2.0.CO%3B2.

Line 256-264: How were these performed? Cite / refer to the tools and parameters used at each step. Again, QIIME, R packages? Other scripts?

Line 262-264: Unclear to me why this combination of analyses are being used. Specifically, why perform a post-hoc test after Kruskal-Wallis?

Line 408: “OUT” should be “OTU”.

Lines 513-517: Maybe, though the sample size is quite low. Not entirely convinced, as the proper approach for determining community assembly is to perform a longitudinal survey. This feels more like a cross-sectional study, with location (pooled data) and sampling time conflating any robust findings. If I am mistaken, please clarify.

Lines 553-560: I think the authors are assuming that microbial host specialists (if there are any) will be bound to the gut lining. This may not always be true. Bacteria are motile organisms, and like trout swimming upstream, can swim in the opposite direction of fecal passage. Thus, it could be possible that microbiota can be host specific, yet reside within or on the surface of fecal material as new material is formed. With any metabolomic cross talk still occurring. I would assume that bacteria attached to the gut lining depend upon what is in the gut. So, very much like the monsoon and dry seasons of desert landscapes, the same can be said here. That is, I would expect the abundance and type of microbial species remaining on the lining of the gut to become more depauperate. Thus, we are looking at the microbiota of the gut lining that can deal with “droughts”, not necessarily those that may be able to remain.  It’d be great if the authors can speak to this. Especially, considering the strong assumption that host specificity is tied to being able to “attach” to the gut lining. To be sure, this is a reasonable assumption, but not sure how well vetted this assumption really is…

Lines 570-584: Need to refer to the figures / tables throughout this section.

Lines 583-586: This is the major weakness of the study. Although acknowledged by the authors, they maintain emphatic statements throughout the manuscript, e.g. “This result contradicts the hypothesis that dragonflies impose strong positive selection favoring a specific, shared set of functionally important bacteria”. Which is a bit disingenuous. You cannot have it both ways. I suggest that the statements be made less emphatic.

Lines 595-600: Why not test some of these potential associations in part? There are a variety of approaches. Blombergs K, UniFrac, Phylofactorization, etc… Some other examples: can map microbial community alpha diversity or microbial community states (i.e. microbiotyping) with host phylogeny.

Line 621-623: This is great, and I largely agree with this! I feel that this point should be made more clearly as potential outcome. This partly ties in with my comments about microbiota that may live in/on the fecal material rather than be attached to gut lining. To be honest, this point (diet specialization is a strong driver of gut bacterial communities)  is a bit lost throughout the entirety of the manuscript. Perhaps this lack of clarity is due to too much reference to neutral assembly. This leads the reader, including this one, to assume that the point being made has to do with lack of differences in microbial communities among the dragonflies across the regions. This appears to not be the case. The microbiota are different, but not due to host species type, or geography, but due to diet.

Line 632-633: This statement, on the surface, seems to contradict what was referred to in my previous comment. I’d recommend being explicit by stating / restating that although microbiota are transient, with likely limited impact on the host, they are indeed driven by diet (i.e. nutrients available to the microbiota). Alternatively, could there be alternate stable states of gut microbiota?

Line 639-641: True, but selection for what. Remember selection is contextual. Selection can be occurring, but is a culmination of, season, diet, host, etc… The microbial communities are different because of different diet….

Line 646-648: It sure will. This is exciting research!

Fire S1 – should place within the figure legend the number of samples.

Supporting file line 122: should be “closed reference”


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: HOST DIETARY SPECIALIZATION AND NEUTRAL ASSEMBLY SHAPE GUT BACTERIAL COMMUNITIES OF WILD DRAGONFLIES
Review round: 1
Reviewer: 2

Output:
Basic reporting: I found this paper easy to read, with clear writing and appropriate literature citations.
Experimental design: Experimental design is impressive, even though the spatial and temporal resolution of the study are somewhat limited for reasons of practicality.

I also commend the authors for presenting their findings even when their FISH experiment did not show strong results.
Validity of the findings: The authors do a good job of explaining their findings in context of the limitations of their study. The discussion of spatial and prey patterns in their gut microbiome data is appropriately nuanced, and the authors set up themselves or others nicely for future studies looking at environmental conditions (temperature, vegetation, etc) that may be underlying the large effect of sample site reported here.
Additional comments: I only have minor comments on this manuscript, as I do not have any major concerns. I will note that I am not an expert in the field of entomology and I do not have much experience with FISH, so I will not comment on those areas of the manuscript.

L48: What does "through conspecifics" mean in this context? Does it refer to interactions with conspecific dragonflies? Please clarify.

L76: This sentence seems to imply universality in the environmental/host/geographic factors structuring andimal gut bacterial communities. However, it is more likely that assembly mechanisms are very different depending on what species of animal is being considered.

L97: It is unclear what the indiabiodiversity.org citation is for. Please clarify within the parenthetical.

L199: Please specify what version of QIIME software was used, and whether there was a specific protocol or pipeline that was used. Reference to a paper from which the authors drew bioinformatic inspiration would also be fine.

L202: Citation for Fast-QC?

L245: ADONIS is in the R package "vegan"

L246: Please explain what "near-zero variance" means and why it was desirable to remove it from the data.

L293: I agree that within the authors' experimental design, OTUs can occur at a higher frequency within host than expected given the "metacommunity" of OTUs found across all hosts (positive selection). To be clear, the actual metacommunity is the pool of OTUs that are reasonable to assume could be found inside dragonfly guts, and this metacommunity is only estimated by the pool of all OTUs found in the study (L276). However, I do not agree that negative selection can be inferred by this study. An OTU cannot be both "abundant within the metacommunity" and "occur in only a few individuals", because for that OTU to be abundant in the metacommunity it would have to occur within many individuals. This comment is not a major issue for me, because the authors do not discuss negative selection in any significant manner.

L376: Consider using "collectors' curves" instead of "rarefaction analysis" since this is the language used earlier in methods (and I think it's a clearer term as well)

L407: clarify what "environmental factors" are or could be, since the term is vague.

L446: it would be helpful to describe beta-diversity in this context as within-group (within-site) variability.

L502: Unclear how binomial model indicates that dispersal (instead of environmental selection) contributes to beta diversity

L551: citation for host selection stabilizing communities in the face of env variation?

L558: Consider rephrasing "predominantly neutrally assembled" with "neutrally assembled with regard to host species", since community assembly is certainly not neutral with regard to sample site and also could be (and is likely) under selection by unknown environmental factors. Same on L624.


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: HOST DIETARY SPECIALIZATION AND NEUTRAL ASSEMBLY SHAPE GUT BACTERIAL COMMUNITIES OF WILD DRAGONFLIES
Review round: 2
Reviewer: 1

Output:
Basic reporting: English writing and content is clear.
The authors updated literature references as requested.
Raw data is easily accessible. Kudos to the authors for providing, not only links to the raw data, but their OTU tables too.
Results and author conclusions appear to be commensurate.
Experimental design: The authors went above and beyond clarifying their approach.
The authors were quite thorough, given the study system, in their approach to combine field sampling, FISH, diet analysis, and a 16S rRNA microbiota survey.
Research does provide a great foundation to start compelling research with insect host-gut relationships.
Validity of the findings: All raw data appear to have been provided. I assume the figshare links to the OTU tables will be released upon acceptance of the manuscript (I was unable to access them).
Conclusions, and associated caveats, were well described and highlighted. I greatly appreciate the authors due diligence in this regard.
Additional comments: I would like to thank the authors for their diligence and thorough response to the reviewers concerns and comments. I am more than satisfied with their considerate responses. I think the revised work is more clear and quite compelling. The willingness of the authors to redo some of the analysis, just to confirm their findings was quite refreshing. I’ve nothing more to suggest / add to the manuscript. I wish the authors best of luck in their research.


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: HOST DIETARY SPECIALIZATION AND NEUTRAL ASSEMBLY SHAPE GUT BACTERIAL COMMUNITIES OF WILD DRAGONFLIES
Review round: 2
Reviewer: 2

Output:
Basic reporting: No issues here.
Experimental design: Still looks good to me. Authors adequately addressed my requests for clarification where appropriate.
Validity of the findings: Authors present their findings in a very straightforward and honest way, and refrain from over-interpreting their results. No problems here.
Additional comments: All my issues with the paper have been addressed.


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: A RECOMBINASE POLYMERASE AMPLIFICATION-LATERAL FLOW DIPSTICK ASSAY FOR RAPID DETECTION OF THE QUARANTINE CITRUS PATHOGEN IN CHINA, PHYTOPHTHORA HIBERNALIS
Review round: 1
Reviewer: 1

Output:
Basic reporting: The writing is clear and although I am not a native english speaker, it seems to me that professional English is used.
The littererature references are adequately quoted, although some of them should be discussed and compared to the results obtained in this study. In particular, the advantages/drawbacks of the tests already available in the literature should be discussed, and not only from the turnaround time for analysis perspective.
The structure of the article is adequate, and the figures are informative and of very good quality. An additional figure showing interspecific polymorphisms within Ypt gene would be welcome though (see general comments).
Experimental design: The authors do not justify the choice of Ypt gene as a target for this new species-specific test. This should be indicated.
The way or rationale that primers and probes have been designed and the final set selected is not sufficiently described. It means that the selection of the primers and probes would not be easy to replicate by others.
Although the RPA technique was developed by other research teams, as quoted in the manuscript, it would be good for the reader to get a reminder of how it actually works. Most of the readers, including myself, are not familiar with this technique and it would be interesting to have more information about that, rather than quote article(s) to refer to.

As we are dealing here with a quarantine pathogen, the specificity and sensitivity of the test is of paramount importance. I believe that the specificity of the test has been unsufficiently addressed here, and verification of this performance criteria should be improved with a larger and more relevant set of fungal strains (see general comments). Also it would have been interesting to check whether the specificity (not only the sensitivity) remains optimal with disturbed parameters (i.e. duration increased, temperature decrease, etc.), as may occur during routine use.
Validity of the findings: Raw data about the selection of primers and probe should be made available (sequence alignmements, number of sequences and strains used, etc.).
Additional comments: Although I do not question at all the validity of the finding, i.e. a set a primers and probe that enable amplification of P. hibernalis DNA, I feel that the current version of the manuscript only contains a limited amount of information regarding the selection and design of the primers and probe, and insufficient data regarding performance criteria.
Although RPA is not a widely used technique, it looks very promising indeed. The reader may like to get more information about how it works. The experimental process used to design and select the primers and probe is not described enough here. One should have more information about the selection of the YPT1 gene among other genes, which types of polymorphisms were targeted by the oligonucleotides, etc. A shortcoming of this study is the lack of information about the selection of species-specific oligonucleotides. The reader should know how many sequences were used for alignment of Ypt gene sequences, how many and which species were represented.
The meaning or role of the different features of the oligonucleotides (e.g. labels, spacer, base analog) should be described. In addition, what is the role of the labeled probe, since there is apparently no fluorescence monitoring during the run? Does it bring an additional level of specificity or is it only used for amplification of part of the gene (as can be read L79-80)?
There are two DNA amplification kits reported (‘TwistAmp DNA amplification kits’ and ‘TwistAmp nfo kit’). It is unclear why two different kits were used, at different steps of the selection and use of the primers and probe.
Regarding the wet lab validation of specificity, a quite large range of Phytophthora species were assessed, but one may regret that few Clade 8 Phytophthora species were included (i.e. P. lateralis, P. foliorum). Although they are unlikely to be found on citrus, they are genetically very close, and the specificity of the test should be demonstrated with closely related species. In the same vein, fungal species frequently found on citrus fruit should have been included in the specificity assessment. Why including only genera and species that are not citrus pathogens or endophytes? It would be good to include species causing lesions on citrus fruits or commonly found as endophytes and check that their DNA does not yield cross-reactions and false-positive results.
Also it would have been interesting to check whether the specificity (not only the sensitivity as reported) remains optimal with disturbed parameters (i.e. duration increased, temperature decrease, etc.), as it may occur during routine use. One may imagine that less stringent parameters might unfortunately enable a weak amplification of non-target DNA, and in consequence, a faint band on the strip. A test targeting a quarantine pathogen deserves careful validation.

The protocol followed to extract DNA from fruit lesion should be a bit more detailed. One should not have to go back to another article (Wang et al.) to have the practical information. In addition, in the manuscript (L146) it is not clear what kind of fruit tissue are used for DNA extraction (the ones that were plated before?), and how they were crushed.

The assay developed in this work is aimed at being used "to detect the quarantine pathogen P. hibernalis in diagnostic laboratories, plant quarantine departments, and customs, especially under time- and resource limited conditions. " RPA technique probably meets these requirements, but there are no data in the paper that demonstrate its cost-effectiveness and robustness for instance. This would be good to discuss.
Last, the discussion section looks a bit meager, and would benefit from comparison with other P. hibernalis detection tools available in the literature. A critical review of potential pitfalls of the different techniques (including RPA of course) would be appreciated.


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: A RECOMBINASE POLYMERASE AMPLIFICATION-LATERAL FLOW DIPSTICK ASSAY FOR RAPID DETECTION OF THE QUARANTINE CITRUS PATHOGEN IN CHINA, PHYTOPHTHORA HIBERNALIS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The manuscript is written in clear English, structurally conformed to the format of PeerJ, and self-contained.
However, the authors need provide sufficient field background/context:
1. Line 38 to 41: The authors should have an accurate description of P. hibernalis: the disease and host range.
2. Line 62 to 63: The authors need to have sufficient background information on the lateral flow assays in the “Introduction”: the principle of the lateral flow immunochromatographic assays; why and how does the LFD accurately detect the target amplicon from the RPA; can the LFD be used to quantify/semi-quantify the target amplicon from the RPA? This is very important for the readers to understand the methodology of this manuscript.
The tables and figures are relevant to the content. My main concern is:
3. Fig. 3: The data shown in Fig. 3 are all included in Table 2. So I suggest the authors to only keep Table 2 in the manuscript.
I have some suggestions on the content and labeling of Table 1 and Fig. 2.
Experimental design: The authors clearly explained the reason and advantages to developing a RPA assay for P. hibernalis detection, however, as I mentioned before, they need to provide sufficient background information on the lateral flow assays to justify the utilization of LFD test.
In “M&M”, some more details, information, and explanations need to be added/addressed:
4. Line 80: I don't understand why a species probe was designed and how it was used in the RPA-LFD assay. Please explain.
5. Line 134: The authors tested the specificity of their RPA-LFD assay against other Oomycota and fungal species, however, they did not include Phytophthora citrophthora, which is an important citrus pathogen (Erwin & Ribeiro 1996; Graham & Menge 2000). Please explain why you did not include P. citrophthora isolates.
6. Line 137 to 146: About the inoculation of orange fruit by P. hibernalis agar culture plugs, did you put the plugs (1cm x 1cm) into the wound (made by a needle) or on the wound? How to secure the plugs if you put it on the wound? According to Erwin & Ribeiro (1996), the maximum growth temperature of P. hibernalis is <25C, I’m wondering what symptoms you observed after 5 days at 25C. What tissue type did you sample? (peel or flesh?). I assume the agar culture plug was removed when sampling? Or it was dried out? I think using a zoospore suspension of Phytophthora spp. may be a more preferable method for fruit inoculation, because it’s easy to quantify and more comparable to the infection occurring in nature.
Validity of the findings: In “Results” and “Discussion” parts, the authors described/explained their data from the experiments, and stated their conclusions. I think there are a few major gaps/concerns that need to be addressed.
7. Line 175: What were the typical brown rot symptoms you observed on the fruit 5 days after inoculation at 25C? P. hibernalis has lower optimal growth and infection temperatures (<20C).
8. Line 176 to 178: In Fig. 4, P. hibernalis mycelial DNA 20 ng was used as the positive control. The total DNA of the infected orange fruit tissue used for RPA-LFD was also 20 ng as described in the M&M. The total DNAs of the infected plant tissue should contain a large portion of plant DNA, which makes the pathogen DNA much less than 20 ng when loading 20 ng total DNA. Please explain why the intensity of test lines of the symptomatic fruit samples were as intense as the positive control.
9. Line 199 to 200: To validate this conclusion, the authors need to 1) explain how the RPA-LFD assays quantify the target sequences; 2) discuss the validation/optimization PCR reactions using the newly designed primers
10. Line 189, 203 to 205: The authors stated that the RPA-LFD assay has great potential of use for specific detection of P. hibernalis on field samples/citrus fruit. However, they only tested the assays with inoculated orange fruit tissues. I think they should have tested the assay on some other field samples. It will be interesting to know if the plant DNA will affect the sensitivity of RPA-LFD assay to detect the pathogen DNA.
11. Line 207 to 211: The PRA assay developed here still requires a sample DNA extraction step before the test, which requires the molecular skills to accomplish. In Miles et al. (2015), they used crude extracts of field samples to validate their Phytophthora genus/species specific RPA assay. I want to know what the author thinks about this method.
Additional comments: Please see above and the attached pdf file for my other comments and suggestions.


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: A RECOMBINASE POLYMERASE AMPLIFICATION-LATERAL FLOW DIPSTICK ASSAY FOR RAPID DETECTION OF THE QUARANTINE CITRUS PATHOGEN IN CHINA, PHYTOPHTHORA HIBERNALIS
Review round: 1
Reviewer: 3

Output:
Basic reporting: •	The paper is clear, and the language used is correct for the target audience.
•	All the references are relevant for the purpose of the paper, and I only suggest the authors to consider citing the reference below to put P. hibernalis in the context of the other Phytophthora species to understand the selection of the isolates for specificity and the design of the assay.
o	Martin, F. N., Blair, J. E., & Coffey, M. D. (2014). A combined mitochondrial and nuclear multilocus phylogeny of the genus Phytophthora. Fungal Genetics and Biology, 66, 19–32. http://doi.org/10.1016/j.fgb.2014.02.006
•	All Figures are relevant and I will suggest to additionally present other information in a supplementary material (see below).
Experimental design: •	The experimental design is consequent with target of the paper, the authors have done a good job on following logic steps for developing and validating the isothermal amplification assay for the detection of P. hibernalis.
•	The scope and the goal of the paper are pretty clear, and the authors managed to demonstrated the functionality of the assay developed. The only limiting factor will be the use of the test on real samples that could potentially be infected with P. hibernalis.
•	Methods are described clearly, and these could be reproduced with detail described by the authors.
Validity of the findings: •	All the findings of the paper are valid and provides a novel assay to detect Phytophthora hibernalis using isothermal amplification with minimal requirements, which could be really useful on limited setups and for control of plant material imports.
•	All the data has been provided.
Additional comments: The paper by Dai et al. provides a development in diagnosis to scout plant material for P. hibernalis and the authors have done a good job on describing the development process, validation and further use of the test using material inoculated in lab conditions. The papers is well written and it is simple enough and easy to follow for the most part. The paper is very concise, and the results are presented in clear way.

I would like to have screening of real samples, like the original sample that was used as source for the isolate 9099. However, the pathogen is not present in China and that could be a limiting factor. Nonetheless, the assay seems to work on most artificially inoculated samples.

Most of my comments are minor and these could be easily addressed by the authors.

Minor points
•	Line 66 – remove “that of”
•	Line 70 – 80 Clarify or mention how many primers were tested and those could be added in the supplementary material indicating their performance (e.g. no amplification, weak, etc.)
•	Line 81 – 84 and table 1 should list both nfo probe and the fluorescent probe, indicating very clearly were are all the modification including the abasic site or THF site and where are located the fluorophore and quencher.
•	Line 145 -clarify if the isolation media was also V8c or did you use a different media. Also, the concentration of the antibiotics should be included.
•	Line 190 – 202. When comparing the conventional PCR with RPA-LFD, it should be acknowledged that you are using the primers designed for RPA, which are at least 30 bp and these are not optimized for conventional PCR. So it could affect the performance of those, if you did optimize the primers either testing different annealing temperatures or duration of cycles please mention that. Otherwise, you should discuss or acknowledge that issue.
•	Table 2 – I will recommend adding the Clade information for every Phytophthora tested, and sort those isolates by clade, in that way you facilitate the understanding of how some of those isolates were selected since a good number of them are in the Clade 8 were P. hibernalis is classified. I highlighted those in blue as example on the PDF.
•	Figure 2 – you should use the actual amount of DNA rather than using the concentrations or include a note either on the legend or the graph itself that suggest that you used 2 µL.


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: ACQUISITION OF FUNGI FROM THE ENVIRONMENT MODIFIES AMBROSIA BEETLE MYCOBIOME DURING INVASION
Review round: 1
Reviewer: 1

Output:
Basic reporting: Basic Reporting

English needs to be checked and revised.
Examples of sentences with poor English
Lines:39-46 (see minor comments section)
Lines:90-91
Lines:71-72
Line: 89
Lines: 288-289
Lines:293
Lines:325
The current phrasing makes comprehension difficult in places.

Intro and background show the context well and the literature is well referenced and relevant.
However, I would like to see some discussion of literature relating to co-evolution between fungal symbionts and beetle hosts included as a key hypothesised implication of their results relate to
"a weaker co-evolutionary association in the invaded environment or the occurrence of a bottleneck effect after introduction."

The structure is clear and easy to follow.

The figures are generally clear but in Figure 3 the p-value cutoff being used should be mentioned, also it's not clear to me whether each taxon incorporates multiple OTUs or just one.

Raw data is referred to but not (yet?) available online: i.e. BioProject PRJNA524707 - but I expect this will be uploaded later?
Experimental design: Experimental design
The study presents original primary research within the scope of the journal.

The research question is clearly stated: "we tested the hypothesis that the composition of the community of fungi associated with ambrosia beetles is affected by the habitat"

The methods are generally well described but there are a few pieces of missing information:
- The old growth rests are described as "very old" I think a more rigorous age estimate is needed here.
- What percentage ethanol was used?
- What was your PCR protocol? Was it exactly the same as Kostovcik et al 2015? If so, please state this clearly.
- What quality filtering parameters did you use?
- Were OTUs clustered at 97%? Please state in text.
- What BLAST parameters did you use?
- How did you select the final ID from you blast - was it just the top hit?
- It sounds like you ran 3 separate linear mixed effects models - one for each of the alpha diversity index? If so - state this explicitly.
- While I understand that there is a reference provided for DESeq2 which was used to identify the differential presence of OTUs between different forest types, I am not familiar with the method it uses and I think the manuscript would benefit from a brief description of how this analysis is done.
- Also it's not clear to me how the significance of the alpha diversity indices were tested - a p-value is given but not test statistic or df - was it a likelihood ratio test? This needs to be stated.
- How is the percentage of explained variance obtained from the PERMANOVA?

The methods are generally rigorous but I see a few issues:
- Checking traps every 3 weeks is likely to affect the results as DNA will be degraded during this time - how this is likely to affect the results should be discussed.
- I can't see how the authors have accounted for spatial autocorrelation in their analysis, this should be done.
- Why didn't the authors use the UNITE database? Simply blasting against GenBank can lead to taxonomic inaccuracies, especially if the 'top hit' is used. I suggest using Genbank with the LCA approach in MEGAN or RDA against UNITE.
  According to the discussion, the majority of sequences were not identified - the proportion of identified OTUs should be mentioned in the results and I think that this problem should be solved by using a better reference database.
- The authors used FDR to correct for multiple comparisons for the PERMANOVA but not for the linear mixed effects models? - if 3 linear mixed effects models were used this should be done.
Validity of the findings: Validity of findings
I think it's clear that there is a strong difference between the fungal community derived from X.germanus communities from old growth and new growth forests - nice NMDS. And, as stated, although X.saxesenii communities are also statistically different - this is probably just an artefact of having a lot of data points - as shown by the low level of explained variation and discussed appropriately.

It's also clear that there was a difference in the extrapolated richness (Chao1) and phylogenetic diversity between old growth and new growth forests for X.germanus where old growth growth forests have higher diversity in both cases while this was not found for X.saxesenii - this too was discussed.

However, I am not convinced by the discussion of the potential mechanisms behind these findings - i.e. the fact that habitat had a greater effect on the mycobiota of the invasive beetle species indicates "a limited co-evolution between X.germanus and environmental fungi in the invaded area or the occurrence of a bottleneck effect after its introduction". I am not really sure what the authors mean by this and think that this claim needs careful explanation with examples and references.
Additionally, there is no discussion of the 1-Simpson (dominance) results in the discussion and how these results add to the interpretation of what's happening in the system.
In lines 295-296 the authors discuss the effect of natural enemies but it is not clear what they are referring to - I assume entomopathogenic fungi that attack the beetles?
The authors also say that "it is reasonable to assume that the sudden arrival of a species in a novel environment leads to a reduced efficiency of these mechanisms." Again, I would like to see a clearer logical flow here explaining these assertions and drawing in the results of this study.

Finally, something that I really do think needs some discussion, is the fact that these fungi will come from both the gut and the mycangia (assuming the rigorous surface sterilisation did not remove the mycangial community). As such, multiple mechanisms are behind these findings. The discussion in lines 286-292 would benefit from drawing a distinction between these two sources of fungal taxa, as would the discussion in lines 318-320.
Additional comments: Other minor comments:
Line 39: Should be 'Microorganisms as an important facet'
Line 40: Should be 'Insects, like many other...'
Lines 41-42: Should be 'positive (i.e. mutualistic)' and 'negative (i.e. parasitic)'
Line 81: "and/or" should be changed to just 'and'
Line 195 - should be NMDS?

The number of specimens that were retained for analysis, along with the number of reads/OTUs etc... should be mentioned in the results.

The estimates etc... for the linear mixed effects models are not provided - I suggest that these are added to the supplementary materials.

It is mentioned that the old growth forests are "small patches". It has been shown that fragment size can alter the diversity of a community - I think the manuscript would benefit from mentioning this in the discussion.


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: ACQUISITION OF FUNGI FROM THE ENVIRONMENT MODIFIES AMBROSIA BEETLE MYCOBIOME DURING INVASION
Review round: 1
Reviewer: 2

Output:
Basic reporting: I cannot say that the article was clear, unambiguous throughout:
The abstract needs to be reworked to be much more clear. There are a number of concepts in it and it must be better defined.
The introduction includes a number of important concepts and is relevant, but it is also lacking essential concepts to be defined such as;
•	Molecular markers used for fungi, and their pros and cons;
•	Technologies to assess communities (e.g. NGS, metabarcoding);
•	Information related to old growth and restored forests (instead, it was explained it in the Materials and Method section);
•	Insect traps and lures;
Unfortunately, many citations are problematic; I appreciate the authors’ effort in using recently published work but, I noticed many occurrences of “cross-referring” in the article, especially so in the introduction where base concepts were defined. For example, on line 34, the cited authors “Early et al.” are not the original authors of this information. Early et al. do talk about those facts, but the reviewed article’s authors need to cite the originator of this information (e.g. Early et al.'s citation of "Millennium Ecosystem Assessment. Ecosystems and Human Well-being: synthesis World Resources Institute (2005)". The same applies to the citation from Brockerhoff and Liebhold (2017). I will not highlight other similar "cross-referring" occurrences in this article (there are more), but they all need to be addressed, please.
____________________________________________
More than once, I noticed that information stated sounded a bit repetitive or as if the authors were “spinning around” the idea instead of going straight to the point by using repetitive words or more words than needed. The article would benefit from fine-tuning this aspect as it would be easier to read. One example is as follow:
“In addition, exotic insects interact with native microbial communities and thus may acquire novel microorganisms in the invaded environment that may affect their invasion. Understanding the ecological factors that influence the acquisition of novel microorganisms is thus essential to clarify the mechanisms behind insect invasions.”
A statement that could possibly be shortened in something possibly more efficient such as:
“Given that exotic insects interact with native microbial communities, it is essential to better understand i) the ecological factors influencing the acquisition of new microorganisms by beetles and ii) the mechanisms involved.”
In addition, repetition of words is also occurring at times, and there are a few times where I considered the vocabulary inexact. Three examples are presented below:
Repetition:
“All these symbionts represent a main component of an insect invader as can be responsible for the success or failure of its invasion and for the impact that it can have on in the invaded ecosystem.“
Inexact vocabulary:
“In addition, exotic insects interact with native microbial communities and thus may acquire novel microorganisms in the invaded environment that may affect their invasion.”
The word "novel" is misleading as it suggests the acquisition of microorganisms that did not exist before. I suggest rephrasing with something along the lines of "never previously associated with invasive exotic insects" or "newly associated".
“The comparison between the exotic and the native species allowed us to test whether the beetle fungal communities respond equally when facing different habitats.”

What is meant by "respond"? Did the authors actually test the beetle's response or did they seldom compare communities? The term "respond" is suggesting that they looked at behavioral changes, which I don’t think they did.
_______________________
Currently, it is impossible to access the raw data deposited under the NCBI SRA BioProject PRJNA524707 (stated in the article). It is essential that the data becomes available for better reviewing the article. I suspect that the release date is in the future, which prevented me from accessing it.
________________

In general, Tables and Figures were clear, neat, and intelligible; although you will notice a few suggestions to improve some of them.
Experimental design: The introduction needs to be better structured as literature is intercalated between goals and hypotheses statements, which becomes confusing for the reader to understand the goals, research questions and their relevance. Specific examples can be found in the annotated PDF document attached.
----------------------
In general, the science used appears to be sound (usage of known bioinformatics tools and statistical tests, inclusion of controls within the experiment, as well as triplicates, etc.), although given the lack of details on the Materials and Methods, it is hard for me to assess this aspect in a fair manner.
--------------------------
There are details missing with regards to the multi funnel traps used. It would be relevant to specify the color used, the height at which they were installed, the under vegetation type, and whether it was a wet or dry system. I believe authors used the wet system, in which case they shall add more details related to the release system for the lure. Those traps are designed so one can use ultra-high release semiochemicals that are specific to a certain group of insect.
Another concern I had is that the authors used a broad lure to attract specific beetles. Ethanol, if this is the only one that the authors used, is attractive to almost any insects and therefore I wonder if they shall have opted for a better suited semiochemical to target the desired ambrosia beetles.

I find it confusing the way it is written now, as authors mention using ethanol for baiting and then ethylene glycol for killing the insects, but very little details are given as to how are the chemicals set and released in the trap. It would be relevant to clarify how they washed the traps between each collection and what was used to do so.
--------------------------------------
A lot of details are missing in the Material and Methods, including:
•	software used for data analysis;
•	PCR conditions (cycling), reagents, volumes, concentration and instrument used for metabarcoding;
•	Size selection for amplicon cleaning and ratio used (Ampure particles)
•	Details pertaining to the processing on illumina MiSeq (e.g. was it paired-end?)
•	OTU cutoff %
•	Package and function used for specific analysis
Justification for each data analysis process (i.e. authors shall indicate, for example, why they ran the NMSD test.)
__________________

I noticed occurrences of misplaced sentences or statement in the “Material and Methods” section so I recommend that the article’s structure is reworked for improvement. Specific examples can be -found in the annotated PDF document attached.
Validity of the findings: When done, the explanation for part of the results performed was good and relatively clear. However, I believe it is essential that authors add more to their discussion section. More specifically, I think they shall elaborate on the pros and cons of metagenomics, OTUs, and what one shall expect from the results based on this type of analysis process. The primers used can induce biases, the OTU cutoff is quite important for proper identification, the different information extrapolated by the different diversity indices, etc.

Authors performed a decent amount of speculation to explain the differences they observed within their data and I appreciated that. I enjoyed getting an idea of their point of view on the analyses. They stated clearly that it was only speculation of course.
The conclusion could take improvement; I think that there must be a way to give it more impact and highlight better what was found. It was a little bit “plain” in my personal opinion, which is so sad to close such a load of handwork (give it what it deserves!!).
Additional comments: A few times, I requested that authors add reference to the statements they made and/or that they split sentences that are too long; for instance:

“We are aware that this approach potentially leads to amplification biais for Microascales and Ophiostomatales, which includes the main mutualists of the two ambrosia bettle species. However, in this study we did not focus on the main mutualists, which ecology is widely studied, but we targeted the entire mycobiota of X. germanus and X. saxesenii which is less described and might be important aspects of beetles’ ecology.”

On that note, I noticed the use of personal pronoun throughout the article, (i.e. “we”) and I do not recommend doing so as often as the authors did, but this might be a preference thing only.
--------------------
There was sometimes lack of originality, for instance the first sentence of the abstract is about 99% identical to the first sentence of the discussion part. I noticed a lot of word repetition, among other the word “despite”.
--------------------

Authors shall review the references cited; I noticed that “The R core Team” one included two different years. I did not check many more but I suspect there could be errors induced by the software used to list references (Example EndNote).
------------

One thing that struck me was the wording “Forest continuity”: 1) because I had never heard of it, and 2) because although it is part of the title, authors barely ever used in the article. Forest continuity was described somewhat too late in the article, within the Materials and Methods, which left me wondering for a long time what was this article about exactly. Rather, authors used other “synonyms” such has “habitat characteristics” earlier in 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: ACQUISITION OF FUNGI FROM THE ENVIRONMENT MODIFIES AMBROSIA BEETLE MYCOBIOME DURING INVASION
Review round: 2
Reviewer: 1

Output:
Basic reporting: The language was clear – a few minor errors (see edited word doc).

Intro and background show the context well and the literature is well referenced and relevant.

The structure is clear and easy to follow.

The results were relevant to the hypotheses but some of the claims in the discussion were not supported by the results.
Experimental design: The study presents original primary research within the scope of the journal.

The research question is clearly stated: “In this study, we tested the hypothesis that different habitats influence the composition of the fungal community associated with ambrosia beetles, reflecting a potential acquisition of fungi from the environment.”

The methods are generally rigorous and well described but there is an important issue remaining:
BLAST isn’t an identitifaction method alone – it gives a list of hits against a database and there are a number of different ways of selecting the final identity of the sequence. See https://www.ncbi.nlm.nih.gov/books/NBK279690/
A common method is to select a cutoff (i.e. a value below which you disregard matching sequences) and this is often based on the e-value. You can then use the top hit (the matching reference sequence that has the lowest e-value) for the identity of your template sequence.
This will work for some template sequences, but often you will get multiple matching reference sequences that have an equally well matching sequence in the reference database.
In these cases you need to decide how to select the actual identity – often people use the ‘lowest common ancestor’ approach where if you have two sequences matching your template sequence with the same e-value – eg. Fusarium avenaceum and Fusarium bubigeum, your final identity would be Fusarium sp. Because the lowest common ancestor is the genus.
I would guess that what you have done is just to take the identities where there is no ambiguity – i.e. there is only one top hit as that would explain why you have such high numbers of unidentified species.
Validity of the findings: Last time I wrote: “I am not convinced by the discussion of the potential mechanisms behind these findings - i.e. the fact that habitat had a greater effect on the mycobiota of the invasive beetle species indicates "a limited co-evolution between X. germanus and environmental fungi in the invaded area or the occurrence of a bottleneck effect after its introduction". I am not really sure what the authors mean by this and think that this claim needs careful explanation with examples and references.”

I agree that the authors have clarified this point nicely now but I still think that there should be a statement in the discussion pointing out that two beetle species, one exotic, one non-exotic with no replication. While I think that the study should be published, I think it’s important not to overstate the relevance of the findings. In particular the statement in the conclusion that “we showed that the direct acquisition of microorganisms from the environment can modify the microbiome of an exotic species” seems a bit of a stretch to me.
Additional comments: In general, I think that the dataset collected for this project is really nice but that you're trying to say too much about co-evolutionary theory using data that aren’t suitable. This wasn’t clear to me in the last version as I didn’t understand the logical flow in the discussion. I think this could be easily solved by modifying the discussion to say that this study is very much a hypothesis generation exercise – that you've found evidence to suggest that this bottleneck is occurring and here's how this should be investigated further. I can see that you've already done this to an extent but the structure of the discussion is a bit disjointed so this sentiment doesn’t come across strongly enough.


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: ACQUISITION OF FUNGI FROM THE ENVIRONMENT MODIFIES AMBROSIA BEETLE MYCOBIOME DURING INVASION
Review round: 2
Reviewer: 2

Output:
Basic reporting: I can see a significant improvement in this article with regards to the ambiguities I previously raised. The manuscript is far more easy to read and I truly enjoyed it; great work. This applies as well to the abstract and I liked that the title was adjusted accordingly. I did not encounter repetitions or lenghty sentences anymore.

Authors also partially added literature background as I suggested, although they did not for two points I mentioned (i.e. technologies to assess communities (e.g. NGS, metabarcoding) and insect traps and lures) but, given their reasonable response, I will leave it to the discretion of the editor at this point.

Citations that were a concern to me (e.g. cross-citation) appear to have been adressed properly.

As previously stated, Tables and Figures were clear, neat and intelligible.
Experimental design: I appreciate the major restructuration of the introduction and I truly believe that your paper benefited a lot from that. I don't see the staggering of sections previously mentioned, which is well done. To me, it is clear and efficient as it is now. In addition, the details that I requested for were added; thank you.
Also, authors gave me satisfactory answers to my concerns with regars to insect traps, lures used, OTU cutoff and PCR settings.
While I agree that most bioinformatics details were given, I still would like to see in the Material and Mehods which function were used with the packages Vegan, phyloseq and deseq2, especially so because the function used with other packages were named later in this section. This would improve the ability to replicate the process used.
I think authors also must add the citation for USEARCH: I requested it before but it was embedded with another comment of mine, so I suspect authors may just have not seen it then.

The comment that I made in my previsous review "I believe it is essential that authors add more to their discussion section. More specifically, I think they shall elaborate on the pros and cons of metagenomics, OTUs, and what one shall expect from the results based on this type of analysis process. The primers used can induce biases, the OTU cutoff is quite important for proper identification, the different information extrapolated by the different diversity indices, etc. " still applies to this manuscript, but again, given the reasonable reply from the authors, I will leave it to the editor to cut on that.
Validity of the findings: This paper is bringing new data and is surely worth publishing.
The conclusion is still not strong enough to give this paper what it deserves, although it is currently satisfactory.
Additional comments: The sentence ending in line 319 ([...] which instead the guts.) sounds weird. I suggest rephrasing it slighly.


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: IDENTIFICATION OF NOVEL BRCA1 LARGE GENOMIC REARRANGEMENTS BY A COMPUTATIONAL ALGORITHM OF AMPLICON-BASED NEXT-GENERATION SEQUENCING DATA
Review round: 1
Reviewer: 1

Output:
Basic reporting: Nicolussi A. and Colleagues present the manuscript entitled “Identification of novel BRCA1 large genomic rearrangements by a computational algorithm of amplicon based Next-Generation Sequencing data” where they reported a computational algorithm to predict the presence of BRCA1 LGRs using NGS data. The paper is interesting and well organized, the figures and tables are clear, literature references sufficient and the English language is of a good standard. Therefore, it requires minor changes.

MINOR COMMENTS:

1.	Line 43: add a space between  exons and 16;
2.	Line 200: change (Fig.1A) in (Fig.1a);
3.	Legend Figure 3: write c in bold.
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The reserch is original and well defined. The data are robust and the statistical analysis is reliable. Methods are described with sufficient details and informations. However your discussion needs more detail. I suggest that you improve the discussion providing an overview and a comment on the current technologies to detect BRCA1/2 LGRs.


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: IDENTIFICATION OF NOVEL BRCA1 LARGE GENOMIC REARRANGEMENTS BY A COMPUTATIONAL ALGORITHM OF AMPLICON-BASED NEXT-GENERATION SEQUENCING DATA
Review round: 1
Reviewer: 2

Output:
Basic reporting: I have read  the paper by Nicolussi et al. " Identification of Novel BRCA1 Large genomic rearrangements by a computational algorithm of Amplicon-Based Next-Generation Sequencing data”. This study is interesting and focuses on a topic that currently plays a very important growing role in biomedical research and diagnostics. The paper is scientifically accurate, complete and fully comprehensive to the reader. The reference section is adequate, updated and appropriate to back up the points made in the article.
Experimental design: The methodological approaches and techniques used in this study are appropriate. The authors described a DQ-based algorithm able to identify BRCA1 LGRs, translating NGS clinical sequencing via an Ion Torrent PGM platform into a suitable tool. By this approach, applied to a consecutive cohort of 85 uncharacterized probands (validation set), they predicted the presence of BRCA1 LGRs with 100% sensitivity and 100% negative predictive value, identifying 3 novel BRCA1 LGRGs. Moreover, the authors characterized the breakpoints of these 3 novel BRCA1 deletions, involving exons16-17, 21-22 and 20, respectively.
Validity of the findings: Results are original and provide useful information to the field. The authors address an important topic. Given the increasing demand for genetic diagnostics, an appropriate and complete diagnostic screening of BRCA1/2 germline mutations ensuring quality, is a pressing issue.
Additional comments: I have no major comments on this paper. However, I provide several suggestions in order to make the paper more attractive to readers:
•	The algorithm depicted in Figure 4 includes the breakpoints characterization, therefore it may be better to move Figure 4 and its description at the end of the last paragraph of Results.
•	Could the authors check the use of abbreviations: sometimes they are missed.
•	A minor detail is the varying use of the terms CNV and LGRs in Abstract, Figures and Tables, which may be confusing.
•	Could the authors make a comment on whether they feel this approach can be applied to DNA extracted from cancer/tumor tissues?


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: DIFFERENCES IN THE IMPORTANCE OF MICROCEPHALY, DYSMORPHISM, AND EPILEPSY IN THE DETECTION OF PATHOGENIC CNVS IN ID AND ASD PATIENTS
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comments
Experimental design: Although the findings are interesting and relevant, there were some areas that would benefit from additional clarifications, especially the statistical calculations:
1.	For Figures 1 and 2: Perhaps the reader would benefit more by defining the “Absence/Presence of clinical features. Also, please define what an “unselected” group here means and in Line 133 of the text.
2.	Figure 3: Please change the yes and no to in the figures to patients with/without epilepsy. Perhaps, also consider another way of representing this information. Also, please indicate number of samples in each case.
3.	Figure 4: Please show us the actual Logistic regression calculations. For example, the dependent/independent factors used among other parameters.
4.	Tables with p-values: Were these p-values adjusted? If not, please calculate and note the adjusted p-values for each comparison done.
5.	In the "Results" section of the abstract, the authors noted:
“Presence of macrocephaly in the ASD group showed 25% probability of pathogenic CNV finding by logistic regression, but it was insignificant according to Fisher’s exact test.”
How do you explain this difference?

6.	Have the authors picked a particular age group of samples? If so, please note the ages for the samples.
7.	Finally, did the authors consider other confounding variables in either the ID or ASD group comparisons?  For example, was gender ruled out as a confounding factor? If so, how?
Validity of the findings: My comments are as stated above.
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: DIFFERENCES IN THE IMPORTANCE OF MICROCEPHALY, DYSMORPHISM, AND EPILEPSY IN THE DETECTION OF PATHOGENIC CNVS IN ID AND ASD PATIENTS
Review round: 1
Reviewer: 2

Output:
Basic reporting: The article is generally well written.  Coverage of the relevant literature is adequate. The figures do not really add much to the clarity of the text.
Experimental design: The design is simple and clearly described.but I find it inadequate in a number of ways.
1. The definition of comorbity is inappropriate. For instance, if I see a child with Williams syndrome, the heart defect is not a comorbidity, but  is part of the syndrome. Likewise for a child with the 22q11 deletion syndromes, etc. The authors should have simply subdivided their two cohorts of patiens as being syndromic or non syndromic.
2. The level of ID is not specified, while it is likely relevant in predicting the probability of finding or not finding a causal CNV.
3. Likewise, the degree of microcephaly is not specified
4. Dysmorphic features are not defined, neither is the criterion used to assign a patient to the dysmorphic group. For instance, a child with posteriorly angulated ears and nothing else, is he/she considered dysmorphic?
Validity of the findings: The authors have made a number of correct diagnoses. In that sense their data are valid. However, for the reasons stated above,  the interpretation of the data is questionable. The authors tend to overinterpret their results, while in fact there is very little novelty in their report.
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: TWO NEW SPECIES AND THE MOLECULAR PHYLOGEOGRAPHY OF THE FRESHWATER CRAB GENUS BOTTAPOTAMON (CRUSTACEA: DECAPODA: BRACHYURA: POTAMIDAE)
Review round: 1
Reviewer: 1

Output:
Basic reporting: Many sections within the text are not clear, and are indicated in the text attached.

Many parts of the text are repeated in the different sections, without further explanations or new insights. Just repeat of the same text or paragraph.

The authors has provided a table containing the differences between the different species including the two species described but did not refer to the table much. The authors can discuss more on the morphological and adaptations, with inference to their molecular data and the variance event.
Experimental design: The authors should provide more details on the materials and methods:

a) Did they use old collections and newly collected materials? Or just new freshly collected materials for molecular analysis.

b) What and where were their comparative materials when establishing the two new species?

c) Whose protocol did they follow? What were the modifications to the original protocol etc.
Validity of the findings: The results are novel and interesting. However, the authors fail to address their findings in greater depth.

The authors could have also compared their results to other groups of organisms that can be be found within similar geographical ranges to see if these organisms have also experienced similar speciation event etc.

The authors provided figures 13 and 14, there are so much information that can be extracted from these two figures and very in-depth discussion that can be provided but not much has been written about it.

The results, discussions and conclusions are repeats of each other.
Additional comments: This is a very nice project and it is worth pursuing. A lot of information and speculations/hypotheses can be generated from this project.


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: TWO NEW SPECIES AND THE MOLECULAR PHYLOGEOGRAPHY OF THE FRESHWATER CRAB GENUS BOTTAPOTAMON (CRUSTACEA: DECAPODA: BRACHYURA: POTAMIDAE)
Review round: 1
Reviewer: 2

Output:
Basic reporting: There are major problems with language throughout the text. I recommend the authors use an English editing service. There are also too many figures for a manuscript of such a nature, figs. 5 and 10 can be combined, figs. 11 and 12 can be combined, fig. 4 can be combined with another one. Other problems please see attached MS.
Experimental design: no additional comment, see attached MS for details.
Validity of the findings: no additional comment, see attached MS for details.
Additional comments: Please see attached MS for details and revise and make corrections throughout the text, then use a language editing service. I would be happy to review the MS again in detail after these have been done.


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: TWO NEW SPECIES AND THE MOLECULAR PHYLOGEOGRAPHY OF THE FRESHWATER CRAB GENUS BOTTAPOTAMON (CRUSTACEA: DECAPODA: BRACHYURA: POTAMIDAE)
Review round: 2
Reviewer: 1

Output:
Basic reporting: The overall formatting requires a bit of work. The details are in the document attached.
Experimental design: No comment
Validity of the findings: No comment
Additional comments: Please see the details in the main text, and please be consistent in the formatting of the scientific names,  when citing other people's article and in the references.


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: TWO NEW SPECIES AND THE MOLECULAR PHYLOGEOGRAPHY OF THE FRESHWATER CRAB GENUS BOTTAPOTAMON (CRUSTACEA: DECAPODA: BRACHYURA: POTAMIDAE)
Review round: 2
Reviewer: 2

Output:
Basic reporting: The English used has been greatly improved upon using an editing service. However, there are still multiple errors in upper/lower case and wrong punctuation marks throughout the text. There is even a copied paragraph that is out of position. The references are still not in alphabetical order. The scientific names in the tables are not in italic etc… The amount of care into manuscript preparation is insufficient. The morphological description needs to be improved greatly, I suggest you use your teams' previous publications as a reference. See the attached file for details.
Experimental design: Ok.
Validity of the findings: I have some concerns about the measurements and ratios, please check your measuring methods and see if you have to redo all the measurements. See the attached file for details. If possible, use multiple specimens for the same measurement to make up for error. Some characters on your comparison table are highly variable, are you sure they are fit for comparison? If so, please give a brief justification because to my knowledge these characters have not been used before. Please see some recent publications on new Potamidae species to see which characters are useful.
Additional comments: The number of authors has changed from three to four. I am strongly against this (see: Ng, P. K. L. (1994). The citation of species names and the role of the authors name. Raffles Bulletin of Zoology, 42(3), 509-513.). As a referee, I am happy spend as much time as is needed in correcting scientific errors and give advice in basic reporting, but it is not our duty to tidy up a careless mistakes throughout the manuscript, please take care in preparing the manuscript and revise again and again before submitting. I am willing to revise once again after you have responded to all of my suggestions.


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: TWO NEW SPECIES AND THE MOLECULAR PHYLOGEOGRAPHY OF THE FRESHWATER CRAB GENUS BOTTAPOTAMON (CRUSTACEA: DECAPODA: BRACHYURA: POTAMIDAE)
Review round: 3
Reviewer: 1

Output:
Basic reporting: The comments are listed in red inside the manuscript.
Experimental design: no comment
Validity of the findings: The authors need to explain more on figure 11.
Additional comments: Please see the comments inside 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: TWO NEW SPECIES AND THE MOLECULAR PHYLOGEOGRAPHY OF THE FRESHWATER CRAB GENUS BOTTAPOTAMON (CRUSTACEA: DECAPODA: BRACHYURA: POTAMIDAE)
Review round: 3
Reviewer: 2

Output:
Basic reporting: The manuscript is improved, but there are still numerous issues that have not been addressed. For example: In line 293, "The male sternum is relatively flat and has granularwith numerous small pits;. sternites 1/2 fused and triangular; transverse sulcus between sternites 2/3 suture; sternites 3/4 fused without obvious demarcation. " is repeated, this has still not been deleted. In line 306, "third maxilliped without flagellum", but your description and photos show there is a flagellum. Also, you have to be more precise with the comparisons, which characters are only seen in the new species? Which species is the new species closest to and how do they differ? These additional details will be of much use to future researchers.
Experimental design: Same as last review. You MUST check your measurements, it is highly unlikey that the carapace ratio is 1.6-1.7, that is very very wide!
Validity of the findings: Findings are generally valid though the articulation needs to be improved.
Additional comments: Please address all issues I have previously pointed out.


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: HIGH-THROUGHPUT SEQUENCE ANALYSIS REVEALS VARIATION IN THE RELATIVE ABUNDANCE OF COMPONENTS OF THE BACTERIAL AND FUNGAL MICROBIOTA IN THE RHIZOSPHERE OF GINKGO BILOBA
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript describes microbiota of Ginko bilboa rhizosphere and comparison of that with soil microbiota from a similar site. The used language is relatively good. However, field background, context and references used are very limited. In fact, almost no relevant information on previously published rhizosphere microbiota research is provided.
Raw data is shared, the structure of the manuscript is relevant and figures relatively well designed.
With a deep appreciation of the importance of Gink bilboa as widely accepted components of ethnopharmaceutical remedies, the reason why only this one species of plant from only one particular site has been chosen as study object reminds hard to understand.
Experimental design: Experimental design of laboratory work is standard and acceptable, no novel approaches are described.
Sample collection design is very limited and at this moment on an unacceptable low level.
Validity of the findings: Provided findings are relevant per se. However, the novelty of this information is hard to find.
The experiments should have been performed at least in several sites with different soil to give a deeper understanding which specific finding are ginko specific and which soil/site specific. An alternative possibility to make provided findings as meaningful would have been a comparison of several plant species in similar soil type to reveal which findings are in fact gink specific.
Additional comments: This is a technically nicely performed work, that however, does not provide any relevant new knowledge on rhizospehere microbiota as such or specifically ginko rhizosphere microbiota.


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: HIGH-THROUGHPUT SEQUENCE ANALYSIS REVEALS VARIATION IN THE RELATIVE ABUNDANCE OF COMPONENTS OF THE BACTERIAL AND FUNGAL MICROBIOTA IN THE RHIZOSPHERE OF GINKGO BILOBA
Review round: 1
Reviewer: 2

Output:
Basic reporting: no comment
Experimental design: no comment
Validity of the findings: See general comments for minor stats problem.
Additional comments: This paper characterizes the microbial communities associated with the rhizosphere and bulk soil in proximity to Ginko trees. In general, the science is done correctly – the methods are appropriate and the data are fairly convincing in this relatively straightforward study. However, there are multiple presentational problems that need to be addressed according to my comments below, mostly with the figures and tables. Additionally, there are some minor problems with English usage/grammar throughout that need to be addressed – I commend the authors that the manuscript is fairly good, just needs one more round of careful proofreading (esp. for certain turns of phrases).

Specific comments

Throughout: Your scientific names for Ginko and bacteria are missing their proper italics in certain places.

Abstract: In contact with, not “in touch with”. Abundances are simply different and not “altered” unless you have experimentally altered something.

1)	L.93-96: If you did not design these primers yourselves, you should give their names and the references from which they come. If you did design them, you should still give names and coordinates/locations for them on the molecules so that people can compare.
2)	L.122-124: It is important you state what this number is you are normalizing to.

Table 1: A rate is a change in a value over time, so you should be using proportion or simply percentage. Q20 and 30 values are not error rates “less than”, they are exactly 99 and 99.9% confidence in the base calls.

Table 2: Some of your lines don’t add up, such as R-1 that has 30854+204+7028=38086 and not 38089. You also have inconsistencies in the table numbers with commas missing and some periods instead.

General note: Some of the below comments are made about the main figures, but are also applicable to some of the Supplementary Figures and you should adjust them accordingly.

Figure 2: Unless your values are all normally distributed (you should run test), then you should not be using the t-test, but the non-parametric equivalent (Mann-Whitney).

Figure 3: I would not use the arrows in panel A (use a legend or just labels next to them with circles perhaps) as these types of plots can often have vectors on them and these arrows lend one to think of that mistakenly. In panel B, red and green are not a good color combination to have side-by-side due to color blindness.

Figure 4: You do not mention the abundance scaling here, since it appears from your gradient legend that it is a log10 scale (otherwise your numbers are meaningless). Why do you also use 8 colors/shades that are very close to each other (ie: many pairs of reused colors) instead of picking 8 very different colors for your phyla colors?

Tables S2/S3: You have the room in these tables’ headings to write out the full names of the taxonomic levels and not just the one-letter abbreviations.

Table S4/S5: The PD, ACE and Chao1 values can be rounded to the nearest whole numbers.

Figure S9: Are you sure each node represents a species, as you only label the genus and I don’t think I see duplicate genera names?

Figure S10: As this figure is huge, I would only display those functions with at least a certain threshold of mean. “Color of the circles, the relative higher values of the group” does not mean anything – what do you mean here?


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

Input:
Title: HIGH-THROUGHPUT SEQUENCE ANALYSIS REVEALS VARIATION IN THE RELATIVE ABUNDANCE OF COMPONENTS OF THE BACTERIAL AND FUNGAL MICROBIOTA IN THE RHIZOSPHERE OF GINKGO BILOBA
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: No comment.
Validity of the findings: No comment.
Additional comments: As the authors have addressed almost all of my previous comments, see below for the one exception (plus a new comment), I have no further revisions to add.

Specific comments:

Table 1: You still have the proportions listed as "rates", which is incorrect.

Figure S10: I forgot to mention it before, but as a minor comment (since this is for supplemental), I would switch your blue and brown colors since I automatically assumed that the brown was for the soil, but it was the inverse.


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: ASSOCIATION BETWEEN THE DEGREE OF FIBROSIS IN FIBROTIC FOCUS AND THE UNFAVORABLE CLINICOPATHOLOGICAL PROGNOSTIC FEATURES OF BREAST CANCER
Review round: 1
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: In the Manuscript entitled “Association between the degree of ﬁbrosis in ﬁbrotic focus and the prognosis of breast cancer” the authors provided evidences that high fibrosis in tumor microenvironment fibrotic focuses correlated with the aggressiveness of breast invasive ductal carcinoma, further indicating that the degree of fibrosis in fibrotic focuses might be a useful marker of the prognosis of breast cancer. However, as authors noted in the text, some limitations of the study should be considered in future research in this field.
Taken together, the paper is interesting and well-written thus providing some novel insights into the topic. The Manuscript is recommended for publication.