Santiago C Gonzalez-Martinez

Sophie Karrenberg

From populations to subspecies… to species? Contrasting patterns of local adaptation in closely-related taxa and their potential contribution to species divergence

Emmanuelle Porcher

Decision on your preprint "Potential adaptive divergence between subspecies and populations of snapdragon plants inferred from Qst-Fst comparisons" Dear Sarah Marin, Thank you for submitting a revised version of your manuscript to PCI Evolutionary Biology, and for answering one critical question so rapidly. This version has been evaluated by two reviewers, whose comments are hopefully attached to this message (if not, let me know). First, I would like to renew my apologies for the extremely long time it took me to return this decision. This is due to the pandemics, but still, this excuse is of no great comfort to you. As you will see, both reviewers found that the new, and significantly modified, version of your article is greatly improved. The question of the calculation of Qst is now solved, and I agree that it does not modify the main results of your study, such that I will be happy to recommend it for PCI Evolutionary Biology provided you make the few relatively minor changes suggested by both reviewers and myself.

Thank you very much for submitting your preprint for recommendation in PCI Evolutionary Biology.

Best regards Emmanuelle Porcher Recommender's comments

Abstract: the words « potential » or « potentially » appear 6 times in the abstract. It is good to be cautious but surely some of these could be reworded (check lines 21-24 out in particular) Line 249: I am not sure what "linearized" means here Line 263: replace 'last' with 'latter' Lines 282-285: this latter analysis seems to be the most comprehensive, and the one you really need to address your main questions. What is the point of the other Mantel tests described above? Lines 312-317: Could you confirm that the difference in the correlation between trait values and altitude between the two taxa is not due differences in the variance in altitude across populations for each taxon? Is variance in altitude the same for both taxa? Lines 332-336: do you mean that the results obtained via the examination of overlapping confidence intervals are fully consistent with those obtained by the bootstrapping method? If so, this is not entirely clear from this sentence.

Lines 384 and 385: replace two instances of "less" with "fewer" Additional Comments of the managing board: Mandatory modifications. As indicated in the 'How does it work?' section and in the code of conduct, please make sure that: -Data are available to readers, either in the text or through an open data repository such as Zenodo (free), Dryad or some other institutional repository. Data must be reusable, thus metadata or accompanying text must carefully describe the data. -Details on quantitative analyses (e.g., data treatment and statistical scripts in R, bioinformatic pipeline scripts, etc.) and details concerning simulations (scripts, codes) are available to readers in the text, as appendices, or through an open data repository, such as Zenodo, Dryad or some other institutional repository. The scripts or codes must be carefully described so that they can be reused. -Details on experimental procedures are available to readers in the text or as appendices. -Authors have no financial conflict of interest relating to the article. The article must contain a "Conflict of interest disclosure" paragraph before the reference section containing this sentence: "The authors of this preprint declare that they have no financial conflict of interest with the content of this article." If appropriate, this disclosure may be completed by a sentence indicating that some of the authors are PCI recommenders: "XXX is one of the PCI XXX recommenders."

In order to reach a better referencing and greater visibility of your recommended preprint, we suggest you to do the following modifications:add the following sentence in the acknowledgements: "Version 3 of this preprint has been peerreviewed and recommended by Peer Community In Evolutionary Biology (https://doi.org/10.24072/pci.evolbiol.100097)"

• in the Zenodo metadata "Notes" you can indicate: "This article has been peerreviewed and recommended by Peer Community In Evolutionary Biology (https://doi.org/10.24072/pci.evolbiol.100097)"

• in the Zenodo metadata " For word template, please be careful to correctly update all text in these templates (doi, authors' names, address, title, date, recommender first name and family name …). Please be careful to choose the badges "Open Code" and "Open Data" only if appropriate (in addition to the "Open Access" and "Open Peer-Review" badges). If some of the reviewers are anonymous, indicate for example "Albert Ayler and two anonymous reviewer". Indicate in the "cite as" box the right version of your preprint. It is version 3.

For Latex template, main.tex and sample.bib should be filled. Please be careful to choose the badges "Open Code" and "Open Data" only if appropriate (in addition to the "Open Access" and "Open Peer-Review" badges). Preambule_xxx.tex should be modified (comment lines 115, 117) First of all, my apologies for taking so long to do this review. I am happy about how authors addressed my comments and I find that the manuscript is now more comprehensive. Moreover, the new focus considering the two subspecies separately made it more interesting and appealing.

In this second round of revision, I only have a major comment. I am afraid that the equation provided to compute Qst, Vb / (Vb + 2h2Vw), is wrong. The correct denominator of this equation is the sum of the variance among populations (Vb) and twice the additive variance within-populations, which in your case (full sibs) is twice the family variance (Vw), thus the equation should read: Vb / (Vb + 2Va) or Vb / (Vb + 4Vw) or Vb / (Vb + 2h2Vp), with Vp = Vw + Vres. I tried to check out if this is just an erratum by recomputing Qst from the variance components from Table S3 but Qst values do not seem to fit with those in Figure 4 (Qst values themselves are not reported in the manuscript) in any way I compute them. Please, check this out, as it may imply major revisions to the manuscript.

Minor comments:

Ln 35. Replace "subspecies" by "subspecies divergence".

Ln 49-51. Can you be a bit more specific? Ln 100-102. Not clear to me why you would not expect shorter internode length at high altitudes, as I would expect than to only height but also growth rate would be lower (but I am not an expert on this, so I am probably wrong). In any case I like very much this paragraph setting the expected trait variation with altitude.

Ln 111. 'based on trait heritability', a bit weird to express it in this way… perhaps better to say 'based on partition of genetic variance'? Ln 138. I guess that you estimated genetic differentiation using Fst? Can you add this between parentheses? Ln 159. It is perhaps not very important for this study, as climatic data is only used to characterise the populations, but worldclim does notably bad in mountain regions (in particular for precipitation) and alternative climate databases are preferable. S3?). I also miss some discussion on these values and the comparison with values for other plants in the literature.

Ln 323. 'Several traits had similar…' Ln 366-367. I would say that signatures of potential selection were found for only few traits. Do you think this is because low power of the study (CIs for Qst are large, judging by Figure 4) or does it truly reflect the species' biology? Ln 389. Should this section not come before the previous one? (As it talks about overall differences in adaptation patterns across subspecies) Overall, the Discussion section is still a bit reiterative and, towards the end, it puts too much emphasis on adaptive divergence. This is surprising as adaptive divergence was found for only a handful of traits in this study. I think that a section devoted to why the study did not identify adaptive divergence in more traits (some of them with obvious adaptive value, e.g. SLA) and why altitude did not seem to be a major factor for adaptive divergence in this system would be desirable. All in all, this is a very nice paper and hope that authors will be able to deal with the few revisions that are still needed (and in particular to check out that Qst values are indeed properly computed).

Reviewed by anonymous reviewer, 2020-04-09 13:31

The manuscript by Marin et al. has changed greatly after the revision, so that many of the previous comments by reviewers do not apply anymore. In my opinion the new version is a clear improvement, based on what I read in the previous reviews. My review below is thus independent from those.

The paper is an interesting contribution to our understanding of plant adaptive variation (or lack thereof) along elevation gradients and of how recently-diverged taxa could be responding differently to similar environmental pressures. The authors use an Fst/Gst approach, based on a common garden and previous field studies, to study patterns of local adaptation of two subspecies of snapdragons. The approach is sensible in cases like this where reciprocal transplants are difficult. The paper is overall clearly written but there are some aspects of the analysis and results that need clarification:

• Values of narrow sense heritabilities are estimated in the greenhouse across all populations within each subspecies, rather than for each population. Please justify why this done, given that all subsequent analyses are based on population comparisons, and that we know that h2 values are populationdependent. The authors mention in line 234 that caution must be taken with h2 values, but it is not clear how they are being cautious in the analyses that follow. • I would expect that some of the traits included in the analysis are correlated to each other, notably the number of nodes, branches and internode length. The two traits that are found to vary with altitude, nodes and branches, appear to strongly co-vary within species in the figures. I suspect they are developmentally strongly correlated and thus just two sides of the same coin -if this is the case, they should be combined for analysis or the Mantel tests corrected for multiple comparisons. Other comments: The analysis is focused on comparing two closely related subspecies that, I believe, differ mostly in their floral traits. Have there been any previous studies comparing vegetative traits between the subspecies in wild populations? If not is this a new contribution to this system? If yes, it would be very nice to include in the Methods to provide some background, and to explain how traits vary in the common garden when growing at the same altitude compared to in the wild.

Along those lines, the main traits that differ between the two taxa are floral traits, yet the current study is focused on vegetative traits. This is fine and interesting but it requires some justification -why exclude reproductive traits if their comparison could also be interesting in this particular system? Given that the paper is focused on the differential adaptation patterns between the two subspecies, it could be good to add a bit more about what is known (or unknown) on what keeps the two subspecies separate. I see that there is some explanation on this in the response to the previous round of reviews, so it should be relatively straightforward to include a justification for it here. It seems important to rule out that similar mechanisms could be affecting vegetative traits as well.

Line 161-162: unclear, please be more explicit

Minor comments:

Please carefully check the manuscript for style and English. Here are just a few examples: -repeated use of the Word "potential" in the Abstract -word choice: "combined" in line 48; "participates" in line 119; "all traits" in line 340; "comforted" in line 369 Fig S1 : please use the colour codes used in other figures to show the two subspecies Line 165: "across the entire spatial distribution" is unclear Lien 174: sentence on maternal effects: rephrase for clarity Line 192: some of this information on the traits is already in the Introduction so seems redundant; please explain instead how/when traits were measured. Line 221: is the "plastic container" the randomized block? Line 272: Mantel tests -specify that they were run separately for each subspecies Table 1 legend refers to analysis in JMP? Paragraph starting in line 339 needs revision; there is some repletion and awkward phrasing Please check figure numbers across manuscript

Author's reply:

Dear recommender, all files (track changes revised version, clean pci evol biol pdf template, data and R analysis code, LaTeX code) can be found on zenodo open access file deposit 10.5281/zenodo.3821949

Thank you for the opportunity to submit our revised manuscript.

We took into account all your comments and the comments of the two reviewers (in blue in the following text). We brought a particular attention to clarifying the methods (QST calculation).

The suggested modifications improved the quality of the paper. We thank you and the reviewers for your comments and hope that you will find the manuscript suitable for recommendation. Please find below a detailed response to technical requests, recommender comments, and reviewers comments.

We uploaded a version of the revised manuscript where modifications appear in the track changes format so that they can be visualized easily. We also uploaded a clean Latex version of the revised manuscript using the PCI Evol Biol template.

Looking forward to hearing from you.

Regards, for the authors, Benoit Pujol

RECOMMENDER'S COMMENTS

Abstract: the words « potential » or « potentially » appear 6 times in the abstract. It is good to be cautious but surely some of these could be reworded (check lines 21-24 out in particular). Done, we have deleted and/or replaced 4 of them.

Line 249: I am not sure what "linearized" means here. Done, changed to "normalized".

Line 263: replace 'last' with 'latter'. Done Lines 282-285: this latter analysis seems to be the most comprehensive, and the one you really need to address your main questions. What is the point of the other Mantel tests described above? We agree that the last Mantel test that we performed (population pairwise QST and population pairwise altitude differences while controlling for neutral genetic differentiation) is the most important to address our main question. However, Mantel tests are only correlation tests. We believe that the step by step procedure that we used here strengthen our results. The correlation between Qst and Fst was not significant and the correlation between Qst and altitude was significant. As a result, the results of the last Mantel test appear more reliable.

Lines 312-317: Could you confirm that the difference in the correlation between trait values and altitude between the two taxa is not due differences in the variance in altitude across populations for each taxon? Is variance in altitude the same for both taxa? The variance in altitude between subspecies was quite consistent. Yes, we can confirm that the variance in altitude was not significantly different between subspecies (anova p.value= 0.4). We added text to clarify this point in the methods (LL 163-165 and supplementary information).

Lines 332-336: do you mean that the results obtained via the examination of overlapping confidence intervals are fully consistent with those obtained by the bootstrapping method? If so, this is not entirely clear from this sentence. Yes, this is what we meant. We have modified the sentence to clarify this point LL348-352.

Lines 384 and 385: replace two instances of "less" with "fewer". Done TECHNICAL COMMENTS Additional Comments of the managing board: Mandatory modifications. As indicated in the 'How does it work?' section and in the code of conduct, please make sure that: -Data are available to readers, either in the text or through an open data repository such as Zenodo (free), Dryad or some other institutional repository. Data must be reusable, thus metadata or accompanying text must carefully describe the data. Done (data files deposited on ZENODO) 10.5281/zenodo.3821949 -Details on quantitative analyses (e.g., data treatment and statistical scripts in R, bioinformatic pipeline scripts, etc.) and details concerning simulations (scripts, codes) are available to readers in the text, as appendices, or through an open data repository, such as Zenodo, Dryad or some other institutional repository. The scripts or codes must be carefully described so that they can be reused. Done ("read me" listing the data and analysis files and ready-to-run-analyses (R protocols) calling for the data files automatically are deposited on ZENODO) 10.5281/zenodo.3821949 -Details on experimental procedures are available to readers in the text or as appendices. Done -Authors have no financial conflict of interest relating to the article. The article must contain a "Conflict of interest disclosure" paragraph before the reference section containing this sentence: "The authors of this preprint declare that they have no financial conflict of interest with the content of this article." If appropriate, this disclosure may be completed by a sentence indicating that some of the authors are PCI recommenders: "XXX is one of the PCI XXX recommenders." Done In order to reach a better referencing and greater visibility of your recommended preprint, we suggest you to do the following modifications: -add the following sentence in the acknowledgements: "Version 3 of this preprint has been peerreviewed and recommended by Peer Community In Evolutionary Biology (https://doi.org/10.24072/pci.evolbiol.100097)" Done Optional modifications. ==> We advise you to use templates (word docx template and a latex template) to format your preprint in a PCI style. This is optional. Here is the links of the templates: https://peercommunityin.org/templates/ Done For word template, please be careful to correctly update all text in these templates (doi, authors' names, address, title, date, recommender first name and family name …). Please be careful to choose the badges "Open Code" and "Open Data" only if appropriate (in addition to the "Open Access" and "Open Peer-Review" badges). If some of the reviewers are anonymous, indicate for example "Albert Ayler and two anonymous reviewer". Indicate in the "cite as" box the right version of your preprint. It is version 3.

For Latex template, main.tex and sample.bib should be filled. Please be careful to choose the badges "Open Code" and "Open Data" only if appropriate (in addition to the "Open Access" and "Open Peer-Review" badges). Preambule_xxx.tex should be modified S3 but Qst values do not seem to fit with those in Figure 4 (Qst values themselves are not reported in the manuscript) in any way I compute them. Please, check this out, as it may imply major revisions to the manuscript. You are right; there was a transcription error in the methods. Qst should have appeared as QST = Vb / (Vb + 2 h² (Vw + Vres)), as you noted. Very worried, we screened all our R code and detected an error (the Vres was there but the factor 2 had jumped). We re-ran all the analyses. It did not change the results much, the values barely changed. The only noticeable change was one QST value in A. m. pseudomajus, which P-value was not significant by much, that became nonsignificant. Nothing changed for A. m. striatum. In fact, this makes our conclusion on the potential absence of local adaptation in A. m. pseudomajus more consistent, which indirectly strengthened the observed contrast with the potential presence of local adaptation linked to altitude in A. m. striatum. This reinforced our conclusion that different mechanisms are at work in the two subspecies. For the sake of clarity and transparency, we added the values of the QSTs in Table S3. We also provided the code and data with the MS.

Minor comments: Ln 35. Replace "subspecies" by "subspecies divergence". Keywords: done Ln 49-51. Can you be a bit more specific? Done, we added text to provide ecological context to the citations made in the text (LL 48-58) Ln 100-102. Not clear to me why you would not expect shorter internode length at high altitudes, as I would expect than to only height but also growth rate would be lower (but I am not an expert on this, so I am probably wrong). In any case I like very much this paragraph setting the expected trait variation with altitude. In fact, a lower biomass might not be due to a lower growth rate at a higher altitude. We agree that on the one hand, this may be expected because the final biomass or height should be lower at a higher altitude. However on the other hand, plants are also expected to germinate later at a higher altitude, and consequently to have a shorter growth period. These plants might then have a higher growth rate at a higher altitude to reach a lower vegetative biomass required to reproduce in due time.

Ln 111. 'based on trait heritability', a bit weird to express it in this way… perhaps better to say 'based on partition of genetic variance'? Done Ln 138. I guess that you estimated genetic differentiation using Fst? Can you add this between parentheses? Done Ln 159. It is perhaps not very important for this study, as climatic data is only used to characterise the populations, but worldclim does notably bad in mountain regions (in particular for precipitation) and alternative climate databases are preferable. We agree that wordclim might lack some precision in mountain regions. It was nevertheless used satisfactorily in previous work to characterize the ecological niche of A. majus at the level of populations, across the altitudinal gradient in the Pyrenees, and across the species geographic distribution (Khimoun et al. 2013. Evolutionary Ecology 27: 51-64.). We'd rather keep this approach that has been proof tested in previously published work.

Ln 205. I assume that you mean '…the 637 plants that germinated'? (As there should have been 40 x 24 = 960 pots). Please, specify. Yes indeed, we clarified this point by adding "that germinated" in the text.

Ln 221/230/241. '… plastic container ('block') as a random…' Done Ln 231. '…where Vw is the family…' Done Ln 243. Please, see my major comment above. Hope it is just an erratum! See response to major comment above.

I think you would need to report Qst values somewhere in the Results (perhaps adding these values to Table S3?). Done, Qst values have been reported in Table S3.

I also miss some discussion on these values and the comparison with values for other plants in the literature. In the results section, we added text to discuss overall Qst -Fst differences found in our study and those found in the literature (L359-366). We are not aware of any other studies using a Qst-Fst approach on this species or any other Antirrhinum species.

Ln 323. 'Several traits had similar… Done

Ln 366-367. I would say that signatures of potential selection were found for only few traits. Do you think this is because low power of the study (CIs for Qst are large, judging by Figure 4) or does it truly reflect the species' biology? We now mention that "signatures of potential selection were found for only few traits" L392 in the discussion. We added text in the results LL359-366) where we acknowledge the low power of our approach. Significant QST-FST differences were likely very conservative in our study. One must note that our conclusion about A. m. striatum and A. m. pseudomajus differences is robust to this lack of power.

Ln 389. Should this section not come before the previous one? (As it talks about overall differences in adaptation patterns across subspecies) We'd rather keep it that way. We adopted this logical structure following the suggestions made during the first round of reviews. We believe that this logical structure of the narrative is well suited as it goes from observed global patterns (altitude signal) to observed detailed patterns (subspecies and populations) to mechanisms underlying detailed patterns (ecological and then population genetic aspects).

Overall, the Discussion section is still a bit reiterative and, towards the end, it puts too much emphasis on adaptive divergence. We chased the reiterations and removed them as much as we could as to lower the emphasis on adaptive divergence. This is surprising as adaptive divergence was found for only a handful of traits in this study. I think that a section devoted to why the study did not identify adaptive divergence in more traits (some of them with obvious adaptive value, e.g. SLA) and why altitude did not seem to be a major factor for adaptive divergence in this system would be desirable. We agree that these results were surprising. We added text to discuss (i) the power of the analysis (see comment before), (ii) whether other studies found similar QST-FST differences (see comment before), (iii) had already discussed expected trait adaptations in response to altitude in the introduction in the previous version (including SLA), and (iv) added text in the discussion to address the lack of altitudinal signal for SLA in both subspecies (LL413-415). We'd rather not speculate on the adaptive value of A. majus traits that our statistical analysis did not identify as potential candidate traits involved with adaptation. We'd also rather not speculate on the reasons "why altitude did not seem to be a major factor for adaptive divergence" because we already discuss our results that altitude is involved to some extent with adaptive divergence. We hope that additional studies will be able to bring further elements to answer these questions. 5 needs updating (these linear correlations were removed from the manuscript, thus should not be reported in this figure). Also, why Fst in the y-axis? Done, we removed the regression equations, and added text in the legend to specify that these graphs illustrate the relationship formally tested by mantel tests and that the Fst on the y-axis refers to the grey dots.

All in all, this is a very nice paper and hope that authors will be able to deal with the few revisions that are still needed (and in particular to check out that Qst values are indeed properly computed).

REVIEWED BY ANONYMOUS REVIEWER, 2020-04-09 13:31 The manuscript by Marin et al. has changed greatly after the revision, so that many of the previous comments by reviewers do not apply anymore. In my opinion the new version is a clear improvement, based on what I read in the previous reviews. My review below is thus independent from those.

The paper is an interesting contribution to our understanding of plant adaptive variation (or lack thereof) along elevation gradients and of how recently-diverged taxa could be responding differently to similar environmental pressures. The authors use an Fst/Gst approach, based on a common garden and previous field studies, to study patterns of local adaptation of two subspecies of snapdragons. The approach is sensible in cases like this where reciprocal transplants are difficult. The paper is overall clearly written but there are some aspects of the analysis and results that need clarification:

• Values of narrow sense heritabilities are estimated in the greenhouse across all populations within each subspecies, rather than for each population. Please justify why this done, given that all subsequent analyses are based on population comparisons, and that we know that h2 values are population-dependent. The authors mention in line 234 that caution must be taken with h2 values, but it is not clear how they are being cautious in the analyses that follow. We modified the text LL248-252 to clarify this point. In brief, full sib designs provide less precise heritability estimates than full pedigree based estimates. To increase precision, we traded off the detailed information at the level of populations and produced only one global estimate. We then took into account the uncertainty around h² by providing its 95% CI (calculated by using a parametric bootstrap method). We were cautious not to interpret trait h² values in terms of quantified evolutionary potential to respond to selection or to compare them between traits in the discussion.

• The text explains that pairwise relationships were tested with Mantel and partial Mantel tests, but legends of We removed the equations produced by linear regression from Figures 2 and5. These analyses were removed from the manuscript after the previous round of reviews. Figure legends should have been updated accordingly. Plot figures were kept to illustrate graphically informal trends in the data that were formally tested by Mantel tests.

• I would expect that some of the traits included in the analysis are correlated to each other, notably the number of nodes, branches and internode length. The two traits that are found to vary with altitude, nodes and branches, appear to strongly co-vary within species in the figures. I suspect they are developmentally strongly correlated and thus just two sides of the same coin -if this is the case, they should be combined for analysis or the Mantel tests corrected for multiple comparisons. We added text LL410-412 to acknowledge that these two traits are strongly correlated because axillary buds producing branches are located at nodes. We believe that using a correction for multiple comparisons (eg. sequential Bonferroni correction) is not useful here because only one trait (number of nodes) was considered significant. We flagged another trait on the list as being marginally significant. No other trait was found significant. Using a correction for multiple comparisons here such as the sequential Bonferroni correction would therefore give the exact same result.

Other comments: The analysis is focused on comparing two closely related subspecies that, I believe, differ mostly in their floral traits. Have there been any previous studies comparing vegetative traits between the subspecies in wild populations? If not is this a new contribution to this system? If yes, it would be very nice to include in the Methods to provide some background, and to explain how traits vary in the common garden when growing at the same altitude compared to in the wild. This is indeed to our knowledge a new contribution to this system. We are not aware of studies having measured vegetative traits of A. majus natural populations in the wild or in experimental gardens. We therefore cannot compare. As you might already know, research on A. majus conducted to date was mainly focused on floral traits.

Along those lines, the main traits that differ between the two taxa are floral traits, yet the current study is focused on vegetative traits. This is fine and interesting but it requires some justification -why exclude reproductive traits if their comparison could also be interesting in this particular system? We added text in the methods to clarify this point LL212-215. Following the reviewers' rightful request on the first round of peer reviews, we have split the global data set in two, one for each subspecies. As a consequence, we had not enough statistical power to analyze reproductive traits because less data was available (not all plants that grow flower).

Given that the paper is focused on the differential adaptation patterns between the two subspecies, it could be good to add a bit more about what is known (or unknown) on what keeps the two subspecies separate. I see that there is some explanation on this in the response to the previous round of reviews, so it should be relatively straightforward to include a justification for it here. It seems important to rule out that similar mechanisms could be affecting vegetative traits as well. We added text LL151-153 to clarify that frequency dependent selection based on flower colour maintains A. majus subspecies separate. It would however be speculative "to rule out that similar mechanisms could be affecting vegetative traits" in the absence of a dedicated study and in the presence of evidence [from our study] for vegetative differentiation between subspecies [that is by definition correlated to flower colour].

Line 161-162: unclear, please be more explicit We added text L172 to clarify that as a result of sampling populations on different valley and summits, "populations with similar elevation are not geographically closer."

Minor comments: Please carefully check the manuscript for style and English. Done

Here are just a few examples: -repeated use of the Word "potential" in the Abstract This was modified word choice: -"combined" in line 48; changed to "combined the information from"

• "participates" in line 119; changed to "contributes to"

• "all traits" in line 340 removed • Line 192: some of this information on the traits is already in the Introduction so seems redundant; please explain instead how/when traits were measured. Done, we now presented how/when traits were measured.

• Line 221: is the "plastic container" the randomized block? Yes indeed, we added "block" into brackets.

• Line 272: Mantel tests -specify that they were run separately for each subspecies. Done

• Table 1 legend refers to analysis in JMP? Every analysis was done in R on this new version of the manuscript, the legend needed to be updated. We corrected this.

• Paragraph starting in line 339 needs revision; there is some repletion and awkward phrasing Done, rephrased to "Mantel tests showed no relationship between population pairwise QST and FST for most of traits (Table 2). Only population pairwise QST for the germination date in A. m. striatum was significantly correlated with population pairwise FST." LL368-370

• Please check figure numbers across manuscript Done Download author's reply (PDF file)

Revision round #1

2018-10-16

Dear Sara Marin, I would first like to apologize for the time needed to return this decision, which is partly attributable to the difficulty of finding available reviewers in the middle of summer. Your preprint has now been read carefully by two experts (including Sophie Karrenberg (SK), who signed her review) and by me. We all agree that your manuscript addresses and important evolutionary question (patterns of adaptation to altitude), and that the experimental design was appropriate to address this question, such that I would ultimately be willing to recommend this preprint provided you can address the issues raised by the reviewers. Here are the most critical issues I identified, some of which were raised independently by both reviewers:

(1) Definition of local adaptation: both reviewers and I were lost with, or at the minimum confused by, your distinction between local adaptation (the meaning of which seems to vary throughout the paper, see comments by SK) and adaptation to latitudinal gradients, which involves local adaptation in the broad sense, such that individuals with the highest fitness in one location are on average those originating from this location. It is really important that this point is clarified. This may include for example specifying whether you consider local adaptation as a pattern or as a process or both. Another option for clarification would be to follow the first suggestion of SK, which is to focus more on biology and the question of adaptation to altitude, and how to disentangle it from adaptation to other environmental variables, which may vary in space at a finer grain than altitude (or not, see comment 7 by reviewer #2)

(2) SK is worried that pooling the two subspecies might bias your analyses. There again, it is central to provide a solid justification for this pooling

(3) Methodological / statistical issues: both reviewers had several additional questions and suggestions regarding the statistical analyses, which I will not fully list here (although they all deserve attention), but which include for example: (i) How could you estimate the within population additive genetic variance, when the number of individuals and the number of families seem to be similar (i.e. about one individual per family)? (ii) How was the significance of the relationship between Fst (or Qst) and altitudinal differences tested in Figure 3? (iii) On the same figure, can the statistical significance of the differences in slopes be tested? More generally, the two reviewers often requested more details on the methodology (e.g. Qst-Fst comparisons, quantitative genetics analyses…), and I agree with them that some key information is sometimes missing.

(4) While the "Methods" section could be expanded, the two reviewers and I agreed that the text could also be shortened at places, particularly in the discussion.

Thank you very much for submitting your preprint for recommendation in PCI Evolutionary Biology. I hope you will find this feedback, and particularly the very thorough reviews of the experts, useful to revise your manuscript. Reviewed by Sophie Karrenberg, 2018-08-28 18:08

Best regards Emmanuelle

Your manuscript on altitudinal divergence in snapdragon plants treats an interesting and timely question mostly with appropriate methods. However, I do have several difficulties to evaluate the quality of this research because important information appears to be missing from the manuscript. This concerns: I), most importantly, whether there were genetic or phenotypic differences between two subspecies that were apparently pooled here, according to Material and Methods and II) the experimental design such as spatial arrangement in the garden (how plants were arranged in how many containers) that should be taken account of as a random effect in the analyses, as well as crossing design and number of individuals per family used (see comments below). Regarding the subspecies, an explicit analysis would be most helpful (phenotypic and genetic differentiation, for example PCoA or structure analysis, potentially presented in the supplementary material). Pooling of the subspecies would probably only be appropriate if there are no considerable phenotypic differences or genetic differentiation between them. Fst in these analyses is used to reflect putatively neutral genetic differentiation --this might be difficult assumption if the dataset includes subspecies that are partially reproductively isolated from each other. The description of the subspecies in the method section as well as the citations do fuel this concern. Differences in habitat and flower color between subspecies are described -even pollinator-mediated reproductive isolation could be present in this system. Very careful and convincing analyses and explanations would be needed to motivate the pooling. And -if there are no differences between subspecies, would that not suggest that there might just be a flower color polymorphism? It is important to note that, without this potentially troublesome pooling of subspecies, the number of populations would probably be too low for the present analysis and this is why this issue is so critical. Provided that pooling can be justified, and the design clarified, this manuscript could become a good one, however, further improvements in the analysis and presentation are also needed. The main changes that I believe are necessary are:

1) Focus on biology. The paper would be more interesting if focus was shifted from methods and general interpretations to the biology of altitudinal adaptation. This would be facilitated by presenting the trait-altitude correlations first. These results are interesting for all traits, currently they are only presented for 3 out of 13 traits. From that you could move on to more complex analyses to identify the underlying causes of such trait clines. In the current version, there is overall rather little on HOW the traits change along altitude, for example, there are no details on leaf traits, even though there is a lot of literature of variation in SLA (see citations in literature mentioned below). It would also be very good if explicit expectations for all traits or for trait groups, based on the literature, could be added in the introduction. I would also appreciate an introduction ending in specific questions.

2) In the methods part, you write that you used the between family variance component to estimate the within population additive genetic variance for a trait, as is commonly done. However, Table S1 states, for reproductive traits, the total number of families is 372 and the number of individuals is 380, such that you cannot have had more than one individual per family in most cases, unless you used a subset of families with more individuals (I could not find information on the number of individuals per family). With 1 individual per family it should be very difficult or impossible to estimate the between family variance component.

In Table S3 you do not give the within family variance component so I wonder whether what you state as the within population variance component really is the between family variance component. This issue is in need of clarification. It would also be good if you could explain why you have fewer measurements for reproductive traits than for vegetative traits.

3) Methods, QST -FST. I found the description of the QST -FST comparisons, using expected distributions, unclear and in part contradictory (see comments in the text). In particular, it is not clear to me how you arrived at the confidence intervals for QST on Figure 2. It would fit better if you presented the distribution of expected values for QST together with the observed values, this is the method you stated in the methods section. Alternatively, you could change the methods section.

4) Analysis of pairwise data: the Methods section describes the commonly used and suitable analyses for correlation tests among matrices (pairwise data), Mantel tests and partial Mantel tests, controlling for the effect of neutral genetic divergence. In the results however, a regression analysis is presented (Fig. 3) that is not suitable for this type of non-independent data points. The text states that the Mantel test was used to assess significance of the regression -this is not possible. The actual data points are also not displayed, this is a bit worrisome due to the subspecies issue. My suggestion is to re-work this analysis according to the methods described and to display the data points on Fig. 3.

5) (Local) adaptation, interpretation. The interpretation of what constitutes local

adaption is highly variable throughout the manuscript. At some places, the common cautious interpretation of QST -FST analyses, that they can provide hypotheses on traits that may have adaptively diverged due to selection (see for example review by Leinonen et al. 2013, Nature Reviews Genetics) is used. At quite some other places, however (abstract, introduction, discussion, marked in detailed comments), it appears that local adaptation is inferred whenever trait divergence cannot be attributed to either the altitudinal gradient or neutral divergence. I cannot be sure that the text is really meant that way, of course, but I testify here that it reads that way. This interpretation would be incorrect (genetic drift and many other processes could be responsible for trait divergence instead). Any text that can potentially be misunderstood is probably better changed.

6) Interpretation of the results on germination. The corresponding paragraph in the discussion unfortunately appears contradictory and the two types of results, overall QST -FST and pairwise QST -FST have not been compared (see comments in the text). Moreover, the text also appears as if it was not clear to the authors that a lack of quantitative genetic differentiation in traits does not exclude phenotypic plasticity (i.e., this is not really an alternative interpretation). It seems that this part needs adjustment.

7) Interpretation of genetic divergence. You invoke reproductive isolation, when it appears that isolation by distance would be a sufficient interpretation, unless you refer to the subspecies differences here (see comments above and in the text). However, this cannot be evaluated from the data currently presented , as details on genetic differentiation are missing (see above). I suggest that this interpretation is re-worked one a more detailed analysis is presented. 9) Methods are not really new. Throughout the intro and the discussion, the paper reads as if this mainly is a method advancement. This appears somewhat exaggerated, as similar methods have been used before and since a longer time (>5 yrs). I feel that the work of others should be acknowledged much more here, only few citations on such studies that are able to identify selective agents are given (for example, Hangartner et al).

10) Shortening. I find that the text could likely benefit from shortening, in particular in the introduction and discussion, probably to at least to 2/3 of its present length. I have indicated several parts that appear repetitive in the detailed comments.

11) More comments. I have made comments similar to the above comments as well as many further detailed comment directly on the text using pdf commenting tools in Adobe Acrobat. I am not repeating these detailed comments here. Such a list of details would be very difficult to write and read, because the text did not include any line numbers to refer to.

I hope that you will find my comments clear and helpful for further revisions of your work.

With best wishes, Sophie Karrenberg Download the review (PDF file)

Author's reply: Download author's reply (PDF file)

  to select badges. If some of the reviewers are anonymous, indicate for example "Albert Ayler and two anonymous reviewer". In sample.bib, indicate the right version of your preprint. It is version 3. I hope this is clear. Do not hesitate to ask any help if you need. Once you have made these modifications (plus those requested by the recommender), you should upload a new version of the article on the preprint server. Please tell us when you have done so. Thanks. Preprint DOI: https://doi.org/10.5281/zenodo.3628169 Reviewed by Santiago C. Gonzalez-Martinez, 2020-04-10 10:08

  Ln 205. I assume that you mean '…the 637 plants that germinated'? (As there should have been 40 x 24 = 960 pots). Please, specify. Ln 221/230/241. '… plastic container ('block') as a random…' Ln 231. '…where Vw is the family…' Ln 243. Please, see my major comment above. Hope it is just an erratum! I think you would need to report Qst values somewhere in the Results (perhaps adding these values to Table

Figure 2 '

 2 Figure 2's legend. No need to report the regression fits as they are not significant.

Figure 5

 5 Figure5needs updating (these linear correlations were removed from the manuscript, thus should not be reported in this figure). Also, why Fst in the y-axis?

  (comment lines 115, 117) to select badges. If some of the reviewers are anonymous, indicate for example "Albert Ayler and two anonymous reviewer". In sample.bib, indicate the right version of your preprint. It is version 3. Done REVIEWS REVIEWED BY SANTIAGO C. GONZALEZ-MARTINEZ, 2020-04-10 10:08 In this second round of revision, I only have a major comment. I am afraid that the equation provided to compute Qst, Vb / (Vb + 2h2Vw), is wrong. The correct denominator of this equation is the sum of the variance among populations (Vb) and twice the additive variance within-populations, which in your case (full sibs) is twice the family variance (Vw), thus the equation should read: Vb / (Vb + 2Va) or Vb / (Vb + 4Vw) or Vb / (Vb + 2h2Vp), with Vp = Vw + Vres. I tried to check out if this is just an erratum by recomputing Qst from the variance components from Table

Figure 2 '

 2 Figure 2's legend. No need to report the regression fits as they are not significant. Done

Figure

  Figure5needs updating (these linear correlations were removed from the manuscript, thus should not be reported in this figure). Also, why Fst in the y-axis? Done, we removed the regression equations, and added text in the legend to specify that these graphs illustrate the relationship formally tested by mantel tests and that the Fst on the y-axis refers to the grey dots.

  Fig 2 and Fig 5 include regression equations and p values -please clarify what the analysis was.

•

  "comforted" in line 369 changed by "support" • Fig S1: please use the colour codes used in other figures to show the two subspecies Done • Line 165: "across the entire spatial distribution" is unclear removed • Lien 174: sentence on maternal effects: rephrase for clarity . Done, rephrased to: "This intermediate generation of plants grown in controlled conditions allowed us to reduce potential maternal environmental effects that could have otherwise affected plants grown from seeds sampled in the wild." LL184-185

  Preprint DOI: https://doi.org/10.1101/385377 Reviewed by Santiago C. Gonzalez-Martinez, 2018-08-07 20:44 Download the review (PDF file)

8

  ) Literature. The manuscript would much benefit by adding more literature on the analysis of altitudinal gradients and transplant experiments, for example: Luo, Y., A. Widmer, and S. Karrenberg. 2015. The roles of genetic drift and natural selection in quantitative trait divergence along an altitudinal gradient in Arabidopsis thaliana. Heredity 114:220. Halbritter, A. H., S. Fior, I. Keller, R. Billeter, P. Edwards, R. Holderegger, S. Karrenberg, A. R. Pluess, A. Widmer, and J. M. Alexander. 2018. Trait differentiation and adaptation of plants along elevation gradients. J. Evol. Biol. [Disclaimer: these are papers I am an author on--but they really are related here... as are many of the citations in them].

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  The text explains that pairwise relationships were tested with Mantel and partial Mantel tests, but legends of Fig 2 and Fig 5 include regression equations and p values -please clarify what the analysis was.

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Sylvain Charlat

Yannick Wurm

Some evolutionary insights into an accidental homing endonuclease passage from mitochondria to the nucleus

Not all genetic elements composing genomes are there for the benefit of their carrier. Many have no consequences on fitness, or too mild ones to be eliminated by selection, and thus stem from neutral processes. Many others are indeed the product of selection, but one acting at a different level, increasing the fitness of some elements of the genome only, at the expense of the

"organism" as a whole. These can be called selfish genetic elements, and come into a wide variety of flavours [START_REF] Burt | Genes in Conflict: The Biology of Selfish Genetic Elements[END_REF], illustrating many possible means to cheat with "fair" reproductive processes such as meiosis, and thus get overrepresented in the offspring of their hosts. Producing copies of itself through transposition is one such strategy; a very successful one indeed, explaining a large part of the genomic content of many organisms. Killing non carrier gametes following meiosis in heterozygous carriers is another one. Less know and less common is the ability of some elements to turn heterozygous carriers into homozygous ones, that will thus transmit the selfish elements to all offspring instead of half. This is achieved by nucleic sequences encoding so-called "Homing endonucleases" (HEs). These proteins tend to induce double strand breaks of DNA specifically in regions homologous to their own insertion sites. The recombination machinery is such that the intact homologous region, that is, the one carrying the HE sequence, is then used as a template for the reparation of the break, resulting in the effective conversion of a non-carrier allele into a carrier allele. Such elements can also occur in the mitochondrial genomes of organisms where mitochondria are not strictly transmitted by one parent only, offering mitochondrial HEs some opportunities for "homing" into new non carrier genomes. This is the case in yeasts, where HEs were first reported [START_REF] Coen | Mitochondrial genetics. I. Methodology and phenomenology[END_REF][START_REF] Colleaux | Universal code equivalent of a yeast mitochondrial intron reading frame is expressed into E. coli as a specific double strand endonuclease[END_REF]. In this new study, based on genomic experimental data from the fungal maize pathogen Ustilago maydis, Julien Dutheil and colleagues [START_REF] Dutheil | The insertion of a mitochondrial selfish element into the nuclear genome and its consequences[END_REF] document one possible evolutionary pathway for which little evidence existed before: the passage of a mitochondrial HE into the nuclear genome. The GC content of this region leaves little doubt on its mitochondrial origin, and homologs can indeed be found in the mitochondrial genomes of close relatives. Strangely enough, U. maydis itself does not appear to carry this selfish element in its own mitochondria, suggesting it may have been acquired from a different species, or be subject to a sufficiently rapid turnover to have been recently lost. Many elements of the story uncovered by this study remain mysterious. How, in the first place, was this HE gene inserted in a nuclear genomic region that shows no apparent homology with its original insertion site, making typical "homing" a not-so-likely explanation? This question may in fact be generalised to many HE systems: is the first insertion into a homing site always the product of a typical homing event, which implies the presence of an homologous template DNA fragment, or can HE genes insert through other means? But then, why specifically in regions that would be targeted by the nuclease they encode? What is the evolutionary fate of this newly inserted element? The new gene may well be on its way to pseudogenisation, as suggested by the truncation of its upper part, precluding its functioning as a HE, and the lack of evidence of selective constraints through dN/dS analysis; but the mutation generated by the insertion event may have phenotypic implications, possibly through the partial truncation of another gene, encoding a helicase. How old is this insertion? The fact that it has accumulated some mutations makes a very recent event rather unlikely, but this insertion has been detected in only one isolate of U. maydis, suggesting it is not so frequent in natural populations. Whatever the answers to these open questions, that will hopefully be addressed by further work on this system, the present study has revealed that horizontal transmission enlarges the scope of possible evolutionary consequences of HE genes, that may move not only between mitochondrial genomes, but also occasionally into a nucleus.

Revision round #2 2020-04-08 Decision on "The transfer of a mitochondrial selfish element to the nuclear genome and its consequence" by Dutheil et al (doi.org/10.1101/787044).

I thank the authors for their additional work that has clarified a number of points. Although the reviewers both consider the new version as sufficiently revised, I must confess I still have some concerns that I try to summarise below. In brief, with the clearer overall picture we now have in hands, this genomic change looks very much to me like a very recent mutational event, with little, if any, evolutionary implications. It is of interest to note that some HEG can occasionally insert somewhere in the nuclear genome, and I acknowledge that one had to investigate this insertion in more details. But the finding that it is most likely on its way to pseudogenisation arguably mitigates the significance of this observation. I would find it unfair to simply not recommend this study for this reason, but I suggest below some further revisions to try and clarify this point, and avoid giving excessive expectations to the reader. I apologise in advance if some of the issues raised below stem from my too limited knowledge of the system. If this is the case, may be some additional clarifications are needed to make the paper most accessible to a wide readership. I will start with a summary of what I understood, so that the authors can correct me wherever there is a misunderstanding:

• One sequence (called UMAG_11064), present near a telomere of chromosome 9 of the fungal maize pathogen Ustilago maydis, has a mitochondrial origin, as evidenced by: • a strongly AT biased composition • strong similarity with mitochondrial sequences of close relatives (but not present in Ustilago maydis itself)

• More specifically, this sequence is an insertion of a mitochondrial homing endonuclease. It is not clear how this insertion got there specifically.

(I have one question on this point, that can hopefully be addressed in the paper.

The question is general at first: how do HEGs integrate IN THE FIRST PLACE at their homing site? I do understand how HEGs can spread through gene conversion following cleavage; BUT how does the first insertion occur at the target site? In my understanding, HEGs do not themselves carry the capacity to insert; they are DNA cutting enzymes. Strangely, I did not find an answer to that seemingly basic question in the literature; did I misunderstand something? => The question then becomes more specific: how did this HEG insert at this site in the nuclear genome. The authors mentioned in their rebuttal letter that not much can be said on the insertion site; this should then be stated explicitly, saying that we have no idea how the HEG got there; obviously, the answer to the general question above will affect the answer to this specific one).

• The gene is no longer acting as an HEG (anyway, it cannot be, since it is not inserted in a homing site; right?). It has lost the HEG active sites and its start codon. It does have a potential start codon, but it is not transcribed. The dN/dS is hard to estimate because the branch is very short, but it may be high. Most likely, it is on its way to pseudogenisation.

• The integration of this sequence correlates with the possible truncation of a neighbouring gene (UMAG11065), which includes many paralogs in the genome. Some paralogs are coding for fully functional helicase enzymes. May be UMAG11065 was truncated upon the insertion of UMAG11064, maybe it was truncated before (but the later hypothesis is not considered by the authors?). Now UMAG11065 is expressed a little bit.

• Experimental knockout of UMAG11064 has no phenotypic consequence; the knockout of UMAG11065 has some effects in some particular experimental conditions, that may be related to the loss of its activity; (which does not mean this activity is a function maintained by selection). In brief, there is no evidence that UMAG_11065 is functional either.

• The UMAG11064 is only found in this particular strain. This suggests it could be a very recent mutational event. Based on the phylogeny of UMAG11064 and its homologues, the authors suggest the insertion may have predated the split between Sporisorium reilianum and Sporisorium scitamineum, but in fact, (1) the (S. reilianum, S. scitamineum) node is poorly supported and (2) it may as well be that UMAG_11064 came very recently from another source, not sampled here (from a strain that that would indeed branch at that position in the tree). The fact that it is not present in other natural populations argues against an ancient insertion, and against a new functional role.

Could the authors comment on this summary to help us reach a decision? In the additional comments below, I suggest some modifications on the basis of my understanding of the story.

Title

The term "transfer" tends to suggest that the "mitochondrial selfish element" has retained its capacity to act as a such. I would suggest the following: "Accidental insertion of a mitochondrial selfish element to the nuclear genome and its consequences"

Abstract

Some revisions of the abstract would reduce risks of misunderstandings L18: "Some HE genes are found within Group I introns, where they further facilitate their excision". Without further explanations, one wonders here in what sense do the HEGs facilitate excision of the introns. The sentence would also suggest that HEGs alone are not selfish invasive elements, although they are.

Being in an intron just reduces harmful effects. Overall, I would thus suggest to remove this sentence from the abstract.

L22: "HE that integrated into"; I suggest adding again the adverb "accidentally" L24: "or a horizontal transfer". In some sense, transfer from mtDNA to the nucleus is already a horizontal transfer, even if this occurs from your own mitochondria. I would thus suggest "or a horizontal transfer from a different species"

L25: "acquired a new start codon," => in fact, the start codon is just a remnant of a methionine codon that happened to be there; the current phrasing would suggest a new start codon was selected for. Something like this may be more appropriate: "The telomeric HE underwent mutations in its active site and lost its original start codon. A potential other start codon was retained downstream, but we did not detect significant transcription of the newly created open reading frame, suggesting the inserted is not functional."

L29: the last two sentences starting with "This unusual homing event" are problematic in my view. "Creation of two new genes seems inappropriate. The 'homing" term can also be questioned because it should be restricted, in my understanding, to the conversion event following a DSB at the homing site. Here we rather have an accidental insertion event, through an unknown mechanism. Instead of those two sentences, I would suggest a more modest ending of the abstract. First, the absence of the insertion in other strains should be mentioned, as an indication that this event is likely recent and, in any case, not fixed. The abstract could end by stating that such mutations may be important in some cases, although this is not apparently the case here. Something like: "The absence of this insertion in other field isolates suggests it likely represents a recent mutational event, and brings no support for a putative adaptive significance. These findings indicate that mitochondrial HEGs can occasionally insert in the nuclear genome, a particular mutational event that may constitute a source of adaption, although we found not support for such evolutionary implications in that case."

Main text

L58: "using the HEG itself as a template"; if I understood correctly, what is used as a template is the homologous chromosome, which happens to carry the HEG. I find it slightly unclear to state that the HEG is used as a template: it just happens to be part of the template.

L119: "…which suggests that UMAG_11064 is an authentic nuclear gene." It seems to me that the nuclear location of the gene is already well established at that stage by the genome assembly + PCR control. So, to me, this new piece of data (the fact that there is no copy of this gene in the mitochondria) should rather be seen as an argument that the gene was either lost from mitochondria following its transfer, or acquired from a different species.

L136: "The amino-acid sequence of UMAG_11064 matches the N-terminal…" may be an indication of the level of identity at the protein level would be useful here.

L163: "To further assess the possibility that the UMAG11064 gene is evolving under positive selection, …". I would suggest a rephrasing with something like: "the possibly high dN/dS seen in the UMAG11064 branch could be explained both by relaxed purifying selection or positive selection. To assess the validity of these two explanations…" L189: "the cox1 gene seems to be a hotspot of Group I introns in smut fungi"; to make the idea more explicit, I would suggest: "… of Group I introns encoding HEG in smut fungi" L190: "Lastly, intron 1 in S. reilianum was not detected in U. maydis." The next bit of this paragraph deals, if I understood well, with the UMAG_11064 gene alignment. But strangely the paragraph starts with this sentence about the absence of this gene in U. maydis (presumably in the CO1 gene?). It seems to me this information should not be presented here, or not in this way.

L199: "…detected 13 homologous sequences…"; may be use "paralogous" here instead of "homologous' to make it clear that you are looking homologous sequences in the same genome?

L202: Could the authors state why they go for phylogenetic reconstruction here? What do they want to know with this analysis? I can see why it was required for the inserted gene, but it is not see clear for this gene. If it is only part of the dN/dS analysis, it should not pbe presented and discussed in details, and should not make a figure.

L208: "… but rather to its truncation": but this assumes UMAG04486 corresponds to the ancestral form of UMAG11065. Are there good reasons to think this is the case?

L215: "Our results suggested, however, that the UMAG11065 gene evolved under purifying selection (dN/dS ratio equal to 0.342)"; but it seems to me you do not known if this selection regime still holds after the insertion of UMAG11064. The question is: is UMAG_11065 still functional and subject to purifying selection following this truncation. I suspect it is difficult to answer this question with the data in hands.

A remark on figures and supplementary figures legends: it is currently very difficult to follow which figure is which, since the figure numbers are not in the pdf.

Figure 6: It is slightly disturbing not to see UMAG11065 on these pictures, considering it the closest to UMAG11064?

L233: "an ancestor of the two strains 518 and 521"; shouldn't that be "an ancestor of the three strains 518, 521 and SG200" ? But in any case, all these are coming from a single spore in the lab? I think this should be emphasised: only one occurrence of this insertion was found, likely very recent.

L318: "potentially had non-neutral effects"; but this is highly hypothetical; the neutral explanation proposed for the other story by Louis and Haber seems to correspond rather well to the current one.

L321: "However, an alternative start codon was detected,…"; yes, but the gene is not expressed. This would tend to suggest it is not functional.

L333 and following ones: in my view, arguing for an adaptive role is too speculative based on the data in hands.

Preprint DOI: https://doi.org/10.1101/787044

Reviewed by Jan Engelstaedter, 2020-03-24 06:05 I think the authors have done an excellent job addressing the comments made by myself and the other reviewers. In particular, the new figures 2 and 6 are very helpful and I appreciate that the authors have clarified many aspects of their work and have taken on board my suggestion of an alternative evolutionary scenario for HEG transfer. The article raises many fascinating questions and I hope it will motivate more studies elucidating the evolutionary genetics of mitochondrial HEGs.

Reviewed by Yannick Wurm, 2020-04-01 08:35

The concerns have largely been addressed -the paper looks great. As mentioned previously, a density plot of genome sequencing coverage across the insertion, or comparing the insertion to other parts of the genome would add further support (not PCA indeed). As also mentioned, it would strengthen the story but not change it.

Author's reply:

Download author's reply (PDF file)

Revision round #1

2019-12-19

Dear Julien and colleagues, Many thanks for submitting your manuscript "The transfer of a mitochondrial selfish element to the nuclear genome and its consequences".

I now have in hands two reviews, that are both positive on your work, but also highlight some potential points of improvements.

I concur with the suggestions they have made. In particular, I feel a dN/dS analysis, as suggested by reviewer 1, may give support to your suggestion that the inserted gene may be on its way to pseudogenisation. I also found that reviewer 2 made some suggestions that could lead to strong improvements, and would also make your paper more accessible to non-specialists. Just like him, I was wondering what kind of selective forces may turn a HEG to an intron. In that respect, it may be useful to clarify if this type I intron is still able to act as a HEG in the lineages where it is present. In other words, is it correct to denote this elements as a selfish element in its original location and in what respect? It may also make sense to ask why this particular nuclear site became a new insertion site. Can there be any prediction on the specificity of insertion sites? I also concur with Jan to say that horizontal transmission from a different species appears to be the easiest scenario; especially considering the fact that natural strains don' carry the mitochondrial or the nuclear version. Correct? I also found that not enough emphasis was given to the finding that natural strains don't appear to carry this insertion. If this was confirmed, the data may be interpreted as the result of lab rearing conditions, that may allow a slightly delirious mutation -such as this insertion -to be maintained, because of reduced population size or special environmental conditions? I would also suggest computing a tree of the various homologues; this may help the reader to understand the various plausible scenarios.

Finally, I have some minor remarks that are listed below.

Provided that these various comments are taken into account, including those mentioned in their evaluation, but which I have not reported here, I think your manuscript can be made suitable for recommendation by PCI.

Hoping that these comments will seem relevant to you.

Sincerely yours, Sylvain Charlat.

Minor remarks

L57: "As the recognized sequence is highly specific, the insertion typically happens at a homologous position": it should be made clearer that specificity could target any region; but that only those targeting homologous positions do invade. Correct?

L73 (and abstract) "all kingdoms of life": what living groups are referred to here? All domains (bacteria, archaea and eukaryotes) or more specifically different groups within eukaryotes?

How do HEG invade mitochondrial genomes? Is there an equivalent to homologous double strand break repair in mitochondria and chloroplasts?

L126: I assume this is nucleotidic identity? Please confirm.

L127: "Two other very similar sequences…" are they also HEG?

=> A tree showing the different homologs, their assigned functions and origins may be helpful here. This tree should also show the branch where the frameshift most likely occurred.

Sup tabs: I have had difficulties when trying to visualise the tables because there are commas inside definition fields; tab delimited fields would make it easier to read.

Are there good reasons to believe that the ancestor HEG targeted this insertion site?

L177: "suggesting that the latter was truncated because of the UMAG_11064 insertion." But why would the insertion generate the truncation; mays be "following" instead of "because" would be more appropriate?

L184: "Interestingly, this gene family also contains the gene UMAG_03394…" In what sense is this interesting? Is there an implicit that the reader should make?

L197: "The UMAG_11072 gene…" what does this information tell? Is this a positive control? Of what exactly?

L202: wouldn't a secondary loss be equally likely?

One question that could be addressed in the discussion: is there a link between the loss of this intron in CO1 and this nuclear insertion?

With regard to the scenario proposed in figure 7: it seems to me that one should highlight that there is basically no selective explanation for any of the transitions that seem to have taken place. Why did this insertion remain? Why did CO1 lose this intron? Why was UMAG_11065 gene shortened?

L244: "but the former cannot have happened…" unless the nuclear insert comes from another species?

L249: not clear why this hypothesis is not presented as the most likely, on the basis of these divergence levels… I am not sure the arguments are strong enough to suggest that this insertion has any effect, either positive or negative, on fitness. The fact that it appears to be polymorphic does not argue for a strong positive effect anyhow.

L287: "It likely represents a snapshot of evolution, when a mutational event occurred, but selection did not have time yet to act." I don't get this idea. Is it argued that there are selective effects, but very mild ones?

L289: "Its absence in any field isolates of U. maydis sequenced so far…" I had not noticed before that this is only found in the lab. To me, this changes substantially the take home message: it is in fact very plausible that this mutation would be selected against in the field; more generally, the fact that there is no indication of any fitness consequence of this insertion would lead me to take this as an example of a special mutational event. The fact that natural strains don't have the intron and don't have the nuclear insertion either also argues against the view that the intron was transferred to the nucleus => more likely a horizontal transfer.

Could such a transfer have happened in the lab? Are the two species kept in close contact?

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Preprint DOI: https://doi.org/10.1101/787044

Reviewed by Yannick Wurm, 2019-11-25 13:32

Dutheil et al report a fascinating discovery whereby a mobile genetic element which once was an intron of a cox1 gene seems to have excised itself and disrupted the function of a telomeric helicase gene in a strain of smut fungus. The data to support the argument are quite convincing. Intriguingly, this must be a very recent occurrence, because neither event has taken place in close related species or other strains. The manuscript is very clearly written, the methods are solid, and the story shows an elegant example of how a "jumping gene" can produce novel genetic variation in a eukaryote.

Minor comments:

The data to support the integration (genomes assembly + independent PCR) validation are quite strong. I would suggest additionally showing a plot of Illumina sequencing coverage as an additional track of Figure 1B. GC-bias for sequencing may affect this if the library was done based on PCR -an alternative may be to calculate sequencing coverage per gene and to do a PCA similar to Fig 1 but based on sequencing coverage. We would expect the focal gene 11064 to be well within the nuclear cluster but away from the mitochondrial cluster.

The manuscript provides some data (and speculation) about the beneficial impact of having a truncated UMAG_11065. But little insight on the potential costs of the truncation having occurred. A bit more on this would help the discussion.

1) It hasn't become quite clear to me what the significance of the transferred element being an HEG embedded within a class 1 intron is. On line 26 in the abstract the authors refer to the transfer as a 'homing event' but how exactly do they think this came about? In the introduction, the authors explain how, for nuclear HEGs, the HE spreads by inducing a double-strand break in the homologous allele and then getting copied onto the other chromosome. But how does this work when the HEG is in the mitochondrial genome? And how can it effect its own transfer to the nucleus? Is the idea that both a DNA molecule containing the HEG and a HE protein itself somehow made their way from the mitochondria into the nucleus, the then HE cut the DNA in the telomeric region of chr9 which then finally gets repaired by the DNA fragment containing the HE? If so, is there any evidence for this? Does the original telomeric region as found in other strains of U. maydis that don't contain the HEG feature the recognition site of the HE?

2) Perhaps related to the previous, the paper does not seem to be as well embedded into the existing literature as it should be, specifically with respect to the horizontal transfer of introns/HEGs between species. For example, a quick search revealed that several papers, starting in the late 1990s, report horizontal transfer of a cox1 intron between different flowering plants, with probably a fungal origin (e.g., Sanchez-Puerta et al. 2011 BMC Evol Biol 11:277 as well as papers cited therein and subsequent papers). It seems that this literature, which seems very relevant, is neglected here. It would also be good to discuss in more detail previously reported instances of transfers between plasmid and nuclear genomes.

3) The section comparing different U. maydis and S. reilianum strains on p.9 seems crucial for reconstructing the evolutionary history of the transfer event. I was very surprised therefore that in this section (and throughout the paper) no other species of Ustilago was looked at. Ustilago seems to be a large genus comprising several species infecting crops and with full genome sequence data available, so it seems that ascertaining which of these species (if any) also contain the UMAG_11064 HEG in either Cox1 or their nuclear genome should be feasible? Or is the taxonomy misleading in that S. reilianum is actually the closest relative? Specific comments: l.16: I think this is wrong. As described correctly by the authors further down, HEs induce a double strand break and are then copied into the new position via homology-directed repair, so no excision is involved here. (The fact that they often occur within introns that are spliced out of RNA molecules seems a secondary phenomenon.) l.116-17: How well is the mitochondrial genome assembled? Could it be the the gene was missed because of a duplicate in the nucleus? If yes, perhaps the absence of the gene could also be confirmed by PCR? l.120: I would suggest to change "must have occurred recently" to "is likely to have occurred relatively recently". Given that the gene is not expressed there won't be selection to adjust codon usage to the nuclear optimum, and it's also not clear how fast exactly GC content would be driven to nuclear levels.

l.137: Should it read "S. reilianum" here instead of "A. bosporus"? I thought I-AbiIII-P is from A. bosporus, and Fig. 2 shows S. reilianum.

l.150-161 & Figure 3: I was really surprised to see that all introns in cox1 contain an HEG, in both species. Is this typical for fungi or for the gene in general? Also, it is not clear to me why the HEG is "responsible for their correct excision". Is the HE directly involved in intron self-splicing? Aren't there type 1 introns without HEGs as well? l.202: "very recently" is quite vague; it would be good if the authors could be more specific and provide an actual timeframe for this.

l.187-205: I found this section a bit hard to digest, and that shows the phylogenetic relationship between the strains and then graphically shows the configuration of both Cox1 and the chr9 telomeric region for each strain? l.229-232: It seems that no details on the methods used for these assays are provided. Have these assays also been performed in triplicates? Figure 7: I think this evolutionary scenario is plausible. However, given that no strain carrying the HEG in both their mt and nuclear genome was identified, and that horizontal transfers of cox1 introns have been previously reported (see general comment #2), perhaps a simpler scenario of a direct horizontal transfer of the element to chr9, without it ever being present in the U maydis mt genome, would be more parsimonious?

Figure 1 :

 1 Figure 1: Details need to be provided on the plot in panel A. It seems that some kind of principal component analysis was conducted? I guess this is what the authors refer to on l.298 as "within-group correspondence analysis" but as it stands this figure is very cryptic.

Figure 2 :Figure 3 :

 23 Figure 2: It wasn't clear to me what the shading shows exactly in this figure. The caption mentions "level of amino-acid conservation" and I guess is the result of some algorithm implemented in the Boxshade program, based on chemical similarities of amino acids?

  Table 2 didn't help much. For example, in the table pluses indicate the presence of the 11064 ORF in some U. maydays and all S. reilianum strains, but not whether this ORF is part of the Cox1 intron or located on chr9. Also, what does the lack of either pluses or minuses for the 11072 ORF in S. reilianum indicate? Perhaps this table could be replaced by a figure

Authors argue that 11064 is pseudogenizing based on it not being expressed and having several deleterious substitutions. Finding a high dN/dS for it would further support this argument.

Analysis scripts are provided as supplementary -it would be beneficial to put these in a standard centralized, searchable and publicly accessible repository such as GitHub or Gitlab. Some of the text within figures supposes that the reader understands shorthand such as "fw" and "rv" (eg Fig S2)-comprehension would be facilitated if spelling such things out. Similarly, prior to line 227, the meaning of the naming of the deletion strain should be specified unambiguously. Language: -l287: "singularly homogenous" -what does this mean? -l223 a word missing Reviewed by Jan Engelstaedter, 2019-12-18 06:40

In this paper the authors report the transfer of a homing endonuclease gene (HEG) from a mitochondrial intron onto the telomeric region of the nuclear genome of a plant pathogenic fungus. The authors use a wide range of approaches (bioinformatics, phylogenetic, DNA expression analyses, virulence assays) to elucidate this event, demonstrating that the HEG is partially degenerate, not expressed and presumably non-functional but truncated the reading frame of a putative helicase gene that is expressed during infection, with potential impacts on stress resistance. I think these results are very interesting and the methods appear sound. I enjoyed reading this paper and pondering its potential implications for our understanding of genome evolution more generally. I have three general comments and a number of specific comments which are listed below. As a disclaimer I should note that I am not an expert in either homing endonucleases or fungal genetics, so some of these comments may simply reflect my ignorance of the field.

General comments:

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