PONE-D-20-32322

Persistence of the ground beetle (Coleoptera: Carabidae) microbiome to diet manipulation

PLOS ONE

Dear Dr. Kipling

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Reviewers' comments:

Reviewer's Responses to Questions

Comments to the Author

1. Is the manuscript technically sound, and do the data support the conclusions?

The manuscript must describe a technically sound piece of scientific research with data that supports the conclusions. Experiments must have been conducted rigorously, with appropriate controls, replication, and sample sizes. The conclusions must be drawn appropriately based on the data presented.

Reviewer #1: Partly

Reviewer #2: Partly

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2. Has the statistical analysis been performed appropriately and rigorously?

Reviewer #1: Yes

Reviewer #2: I Don't Know

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3. Have the authors made all data underlying the findings in their manuscript fully available?

The PLOS Data policy requires authors to make all data underlying the findings described in their manuscript fully available without restriction, with rare exception (please refer to the Data Availability Statement in the manuscript PDF file). The data should be provided as part of the manuscript or its supporting information, or deposited to a public repository. For example, in addition to summary statistics, the data points behind means, medians and variance measures should be available. If there are restrictions on publicly sharing data—e.g. participant privacy or use of data from a third party—those must be specified.

Reviewer #1: Yes

Reviewer #2: Yes

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4. Is the manuscript presented in an intelligible fashion and written in standard English?

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Reviewer #1: Yes

Reviewer #2: Yes

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5. Review Comments to the Author

Please use the space provided to explain your answers to the questions above. You may also include additional comments for the author, including concerns about dual publication, research ethics, or publication ethics. (Please upload your review as an attachment if it exceeds 20,000 characters)

Reviewer #1: Summary

The manuscript investigates the bacterial community of three species of carabid beetles, evaluating the differences according to insect host, tissue, diet and environment. The dataset is valuable, as there is otherwise scarce research on the microbial communities associated to this beetle family. The consideration of different diets and tissues is additionally relevant. However, from my view there is an important methodological issue that should be addressed, and which might confound the interpretation of the data. Also, the way in which some of the questions are posed, as well as some of the arguments used in the discussion can be misleading. I point out specific issues and suggest some improvements to better align the conclusions with the approach and observations.

General comments

1. In lines 117-118, the authors put forward an aim consistent with the experiments that were carried out, i.e. “This study examined how the transient factor of diet treatment, and more permanent factors including host species and tissue, contribute to the observed variation in carabid associated microbiomes”. However, later in Lines 124-131 three predictions are put forward in relation to whether the communities are non-transient and to potential functions. This, in my opinion, generates confusion as to what can actually be deduced from the data, specially given the experimental approach. To test for non-transient communities, a broader sampling from different life stages and/or across individuals, or at least placing focus on individual variation would be appropriate. I suggest that the authors remain by the narrative in lines 117-118 and are more cautious in the interpretations, as expanded on in several of the next comments.

2. There is an important confounding factor in the methodology: given that the individuals were not cleared of their original microbiota, it is rather expected that the existing communities are not easily replaced. Another very important aspect is the original establishment of the microbial community, which is likely in earlier life stages. Although the authors do bring this point into discussion, I believe there should be much more emphasis on the relevance of the originally established community and the factors that determine that. These are likely confounding factors, which could be tied to host species and tissue, and thus explain the observed results.

3. Also related to the previous point: on what basis was 17 days chosen as an evaluation period? It might indeed be hard to know which duration is most appropriate to see potential changes, but additional information is useful: How long do these beetles spend in their adult stage? How often do they feed?

4. Associating the (partially) characteristic bacterial composition according to host tissue to potential function is rather weakly founded. Authors somehow acknowledge it, but the overall approach of trying to tie function to this kind of analysis is loose /weak (see specific comment for lines 129-131 and line 347). Also, the fact that the sample size from natural conditions are low make it hard to conclude on consistency, which is likely important for function.

5. I suggest reconsidering the conclusion that: “Symbiosis is a possibility, especially in secretory cells” (see specific comment on lines 454).

6. Presentation of the data in the figures and the references to it in the text can be considerably improved. It was hard to relate to each figure (they are not in order and panel letters not always given). The figures can also become more informative, please see specific comments.

7. The methods section, as well as the background information provided in the introduction are clearly written and structured.

Specific comments:

- Lines 25-26: both here and in the discussion (line 418), the “typical” microbial diversity found in “other insect hosts” is rather ambiguous, since there is a relatively broad spectrum of community types, richness and diversity levels across insect orders, and even within orders. Please instead refer to closer groups for comparison.

- Lines 29-31: as mentioned in the general comments, this conclusion is not supported by the data. There is a significant difference in the bacterial community composition in secretory cells according to species (Fig 2b + legend). Also, if the defensive chemistry is different between species (Line 21), it would also not be coherent to expect highly similar communities if they are involved in producing the defensive compounds.

- Lines 77-79: This is not necessarily true. The set of metabolic pathways of two communities with distinct microbial compositions can in some cases match to a good extent. Different bacteria can play similar roles, the same holds for groups of bacteria.

- Line 124: the (1) for numbering the predictions should be placed in line 125, at “…, then 1) diet..” But see next comment.

- Lines 124 – 125: how this is written suggests that the question addressed is whether carabids harbor non-transient microbes. The experimental approach does not address this though (see general comment 1).

- Lines 129-131: True to some extent, but the link to the question of function is quite loose. Especially considering the contrary situation (microbial communities are not random in respect to tissue), since this is still far from indicating function, specially in rather complex microbial communities like those in carabids.

- Lines 147-149: Does this mean that the diets were completely sterile? Please indicate explicitly.

- Line 226: Here and throughout the manuscript, please indicate the specific panel of the figure referred to (e.g. Fig 1B). Also, please reorder to follow the sequential order of the figure numbers.

- Lines 229-230: I suggest mentioning here or in the methods the list of alpha diversity measures that were evaluated.

- Lines 241: I consider it useful to provide these results here or as a supplement.

- Line 307: the four phylotypes hare present in different abundance, not differentially expressed. Please correct.

- Lines 311-314: this is probably easier to express and understand in the context of evenness. This observation and its importance are hard to grasp as currently stated.

- Lines 330-333: as mentioned in the general comments, the experimental setup involved a relatively short period of time and used beetles with an already established microbiota. Thus, I suggest toning down this statement “these findings demonstrate that carabid microbiomes are highly persistent…”

- Line 347: The hypothesis is supported, but the composition in specific tissues is by no means evidence of function. Because the result can be explained by the different physicochemical conditions in each tissue, or the exposure of certain tissues to different sources of microbes (as also mentioned by the authors), this should not be set as a strong proxy for function, but rather mentioned as a side observation which can be addressed differently.

- Lines 354-355: I disagree with this conclusion based on general comment 2. Please reconsider.

- Lines 358-360: this is different to the 2nd hypothesis mentioned in the introduction, or what are the authors referring to? Also, is there a reason to believe that they transmit them between conspecifics? Gregarious or social behavior would be more in line with such hypothesis, not the fact of seeing similarities across individuals. This could also be the case for vertically transmitted symbionts.

- Line 361: referring to co-evolution is a long stretch in this system. Co-evolution would be expected if there is consistent vertical transmission, but there is no evidence for that here, and it is also not the appropriate data set to address this question.

- Lines 404-407: it was not clear to me what the authors mean and how this connects to the previous lines. Please revise.

- Lines 415-416: I believe this is not a fair claim. While the study is valuable for learning about these 3 insect species, these are only 3 of the most diverse group of animals.

- Line 444: does this match the fact that they were found in all species or a specific species? i.e. are quinones produced in all hosts?

- Line 454: I don’t think that this an appropriate interpretation of the data, at least not based on the results shown. If the definition of symbiosis is used: “the consistent association of individuals from different species for all or most of their lifetime”. If the figures provide support that the communities within each species are consistent across individuals from different populations or collection sites, then this conclusion is better supported. The results from the secretory glands just show some degree of convergence in composition, but this is not per se evidence for symbiosis.

- Figure 4. This figure could become more informative and easier to grasp by

o Showing the composition of each replicate, to give a better impression of the amount of variation per individual.

o Separating or arranging the panels to address a single factor (species or tissue) and therefore message per figure

o In panel 4D, it is not so clear why the species are merged if Fig. 2 already shows that there is clear clustering of composition per species within each body part. I suggest separating this per species, and (in line with the point above), make it a separate figure.

- Figures 4 and 5: I suggest labelling the y-axis as “Relative abundance” for clarity.

Reviewer #2: This paper reports carabid associated microbiomes. There are 3 species, 4 diet groups (3 lab, 1 field), and 3 tissues examined (includes partial body). The hypotheses involve development of microbiomes that are specific to beetle species, their chemical defense capabilities, and possible role in evolution of these capabilities.

It is obvious that the authors have conducted a lot of research in this area and are familiar with related literature. The writing is generally clear, well-organized, and understandable. The abstract should be restructured – findings (lines 19-20) are ahead of methods. No mention in the Abstract of gut microbiota across the 3 species, just pygidial gland. Intro, Line 78 – “they” = carabids (right?). Perhaps restructure sentence to make clear.

The biggest problem I have is the n=3 beetles for each of the treatment groups (12) wherein a treatment group is defined by the carabid species (3) and diet treatment (4 including wild). This is OK for a preliminary study, but not a full-fledged study that would support robust conclusions. If this paper is to be published with such a low n, then the writing needs to clearly convey that these are preliminary findings, reduce the level of confidence in concluding statements, and shorten the Discussion considerably.

The second issue is that “soil” or “environment” are not tested in this study, and mention of such needs to be eliminated from the manuscript (see lines 16, 24, 119, 125, 321, 323, 327, 339, 344, etc). Three wild caught beetles do not compare soil or environment with three groups of beetles lab-reared on 3 different diets.

The third issue is the statistics. Is Chi-Square the right analysis for this study? Can you give more details of what data was used for the chi-sq? Was is it a binary presence absence of bacterial taxa or just a single diversity metric? How many taxa were considered? What were the p values for the non-significant tests? When I look at figure 1, I see tissue types have different diversity. And Wild capture partial body maybe different than lab diets. That all makes sense. Beyond that, I don’t know. Figure 2 suggest differences between carabid species for each tissue microbiome. with secretory cells having the least range across species. And diet having little effect. But remember in this type of analysis, its all relative. If you just isolated diet for a single species, you might see distinct clustering there. I’m unconvinced that chi-square can answer to hypotheses proposed in lines 124-131. Did you test randomness by other tests (lines 119-121)? What did you used to explain variation in microbiomes?

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Reviewer #1: Yes: Laura V. Florez

Reviewer #2: No

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Persistence of the ground beetle (Coleoptera: Carabidae) microbiome to diet manipulation

PONE-D-20-32322R1

Dear Dr. Will,

We’re pleased to inform you that your manuscript has been judged scientifically suitable for publication and will be formally accepted for publication once it meets all outstanding technical requirements.

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Academic Editor

PLOS ONE

Additional Editor Comments (optional):

Reviewers' comments:

Reviewer's Responses to Questions

Comments to the Author

1. If the authors have adequately addressed your comments raised in a previous round of review and you feel that this manuscript is now acceptable for publication, you may indicate that here to bypass the “Comments to the Author” section, enter your conflict of interest statement in the “Confidential to Editor” section, and submit your "Accept" recommendation.

Reviewer #1: All comments have been addressed

Reviewer #2: All comments have been addressed

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2. Is the manuscript technically sound, and do the data support the conclusions?

The manuscript must describe a technically sound piece of scientific research with data that supports the conclusions. Experiments must have been conducted rigorously, with appropriate controls, replication, and sample sizes. The conclusions must be drawn appropriately based on the data presented.

Reviewer #1: Yes

Reviewer #2: (No Response)

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3. Has the statistical analysis been performed appropriately and rigorously?

Reviewer #1: Yes

Reviewer #2: (No Response)

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4. Have the authors made all data underlying the findings in their manuscript fully available?

The PLOS Data policy requires authors to make all data underlying the findings described in their manuscript fully available without restriction, with rare exception (please refer to the Data Availability Statement in the manuscript PDF file). The data should be provided as part of the manuscript or its supporting information, or deposited to a public repository. For example, in addition to summary statistics, the data points behind means, medians and variance measures should be available. If there are restrictions on publicly sharing data—e.g. participant privacy or use of data from a third party—those must be specified.

Reviewer #1: Yes

Reviewer #2: (No Response)

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5. Is the manuscript presented in an intelligible fashion and written in standard English?

PLOS ONE does not copyedit accepted manuscripts, so the language in submitted articles must be clear, correct, and unambiguous. Any typographical or grammatical errors should be corrected at revision, so please note any specific errors here.

Reviewer #1: Yes

Reviewer #2: (No Response)

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6. Review Comments to the Author

Please use the space provided to explain your answers to the questions above. You may also include additional comments for the author, including concerns about dual publication, research ethics, or publication ethics. (Please upload your review as an attachment if it exceeds 20,000 characters)

Reviewer #1: (No Response)

Reviewer #2: (No Response)

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7. PLOS authors have the option to publish the peer review history of their article (what does this mean?). If published, this will include your full peer review and any attached files.

If you choose “no”, your identity will remain anonymous but your review may still be made public.

Do you want your identity to be public for this peer review? For information about this choice, including consent withdrawal, please see our Privacy Policy.

Reviewer #1: Yes: Dr. Laura V. Florez

Reviewer #2: No