A toxin-antidote selfish element increases fitness of its host

Decision letter after peer review:

Thank you for submitting your article "A Toxin-Antidote Selfish Element Increases Fitness of its Host" for consideration by eLife. Your article has been reviewed by 4 peer reviewers, including Erik C Andersen as Reviewing Editor and Reviewer #1, and the evaluation has been overseen by Christian Landry as the Senior Editor. The following individuals involved in the review of your submission have agreed to reveal their identity: Michael Ailion (Reviewer #3); Stefan Zdraljevic (Reviewer #4).

The reviewers have discussed their reviews with one another, and the Reviewing Editor has drafted this to help you prepare a revised submission.

Essential revisions:

1) All reviewers noted the lack of controls for the peel-1 edited strain. I believe that backcrossing and whole-genome sequencing will not adequately address the concerns about the modest peel-1 effect and the single CRISPR-edited allele. The authors should either generate another peel-1 edited strain and test this new strain in the same experiments or add back peel-1 to the deleted strain to show that the modest peel-1 effect goes away.

2) Please update the statistical tests to address issues of multiple testing and non-normality.

3) The N2 data in Figures 2 and 3 are repeated. Please note that point.

4) Many of the other reviewer comments can be addressed by toning down some claims and providing more caveats and/or explanations. Reviewers made good suggestions for how to respond to these comments.

Reviewer #3 (Recommendations for the authors):

1. Though the mathematical modeling is interesting from a theoretical point of view, we feel that it oversells the rationale behind the experiments, setting up a "straw man" argument to knock down. Also, the modeling relies on rather high assumptions of the possible carrying cost of peel-1/zeel-1. For example, the modeling of the effect of outcrossing rate on peel-1/zeel-1 frequency assumes a selection coefficient of 0.35, which seems rather arbitrary and high. Where does this number come from? Is there any precedent for this high carrying cost? In our opinion, the idea that energy expenditure or leaky toxicity accounts for such a high carrying cost seems unlikely.

2. The two studies cited for "outcrossing rates typical for C. elegans" estimated vastly different outcrossing rates (~20% or ~1%). The model presented in Figure 1S2 specifically uses the lower estimates (0-2%), so the Sivasundar and Hey paper is miscited here. It is unclear whether there is a good rationale to go with the lower rate estimates. It would also be helpful to the reader if the value for these outcrossing rates is provided in the main text. Similarly, it would be helpful to provide in the main text the value for "all but the mildest carrying costs" (line 115).

3. The measurement of body size is unclear in the main text. Only when reading methods did we realize that body size is more of a proxy for growth rate rather than an end-point measurement of worm size. Please clarify this in the main text.

4. What is the temporal distribution of egg laying of the N2 and N2peel-1(null) strains? Based on how the data collection is described in the Methods, the authors should already have these data. Does egg-laying start at the same time in the two strains? The fact that strains carrying peel-1 grow faster but also apparently produce more sperm (which might slow them down) makes an analysis of this worthwhile, especially since fitness depends on when eggs are laid, not just how many. Some more characterization of this fitness trait seems appropriate and useful for beginning to understand how peel-1 may be increasing fitness. The original raw data for egg-laying with numbers of eggs laid at each time point should also be presented in the supplementary table rather than just the total amounts.

5. Line 65: the statement "similar elements have not been identified in obligate outcrossing Caenorhabditis nematodes" is somewhat misleading. TA elements may not have been identified in obligate outcrossing nematodes because of research bias since genetic experiments are easier to perform in non-obligate outcrossers and it is unclear that there have been extensive searches for TA elements in outcrossing nematodes. Furthermore, as the mathematical models in this study suggest, TA elements will spread quickly with an increasing rate of outcrossing. Since a TA element's non-fixation within a species has historically been a prerequisite for its discovery, the rapid TA element fixation that would generally occur in obligate outcrossers would make their identification more challenging.

6. Line 211-212: it is stated that this is the "first measurement of the fitness cost of a TA element to the host" and "first demonstration that a TA element can benefit the organism." These claims may be overstated. It has been previously shown in several cases that TA elements can provide fitness benefits to bacteria, such as improved antibiotic resistance (e.g. Bogati et al. 2022, PMID: 34570627). Also, the use of the phrase "fitness cost" in the first part of this sentence is confusing, since "cost" implies reduced fitness which is the opposite of what the paper shows for peel-1/zeel-1.

7. More details about the CRISPR protocol should be provided. It is unclear whether Cas9/sgRNAs were introduced as RNPs or plasmids (and at what concentrations). It is unclear how worms were screened for edits – the table has columns for primer sequences but these are blank. It is also unclear how many Dpy or Rol worms were screened and how many peel-1 or zeel-1 edited worms were found (the efficiency of CRISPR). The meaning of the shaded portion of the repairing oligo sequences in the table is not explained. Finally, it is not stated whether CRISPR-generated mutant strains were outcrossed.

8. The n values for fecundity assays are somewhat unclear. In the legends for Figure 2C and 3B, it says n=5 or n=6. Intuitively, most readers would interpret this as 5 or 6 worms, but according to the methods, it seems that this is 5 or 6 plates where each plate has a total of 6 worms whose average fecundity is calculated. This should be made clear in the figure legends. And though it says n=6 for the introgressed zeel-1 peel-1 strain, it seems that it is only 5 based on the source data in the supplementary table.

9. Line 185: it seems to be assumed that peel-1 arose before zeel-1, but the basis for this assumption is unclear.

10. Line 191 should cite Seidel et al. 2008 instead of Seidel et al. 2011.

11. The very right side of Figure 2C is cut off, making the rightmost column label incomplete. The legend of Figure 2 is also cut off at the bottom.

12. Figure 2B and 3C data are oversold visually due to the y-axis scale. There is only a 20-30 embryo difference but visually appears much more than that. It would be better to start the y-axis at 0.

13. Raw data for relative fitness experiments should be provided in a supplementary table.

14. The concluding sentence of the Results and Discussion section is unclear to us. What is meant by "outsized?"

15. The concluding sentence of the Conclusion would be better framed as a hypothesis rather than a belief.

16. How were outliers (mentioned in Figure 3 legend) identified/defined in the datasets?

17. Units should be added to column titles in the supplementary source data tables.

18. Line 243: the term "1k" is used but should be written out as "1000" to differentiate it from the "k" parameter used in the model.

19. Line 115: typo – "will likely to be" should read "will likely be".

20. Figure 1A typo: hermaphrodite.

Reviewer #4 (Recommendations for the authors):

1) It is unclear what, if any, experiments PTM573 (dpy-10 barcoded strain with the CB4856 hyper-divergent introgression) was used for. I am wondering why it is in the strain table.

1) Are the data for N2 presented in Figures 2B and 3C the same data? The boxplot distribution seems very similar by eye and without any data tables showing the actual values it is impossible for me to tell. Bacteria prep, agar prep, temperature, humidity levels, etc might affect the results on different days. So if the N2 values are from a single experiment, it might be best to repeat the experiment at the same time with the comparison strain. Ignore this comment if the data presented is actually from two separate experiments where the comparison strain was assayed simultaneously.

[Editors’ note: further revisions were suggested prior to acceptance, as described below.]

Thank you for resubmitting your work entitled "A Toxin-Antidote Selfish Element Increases Fitness of its Host" for further consideration by eLife. Your revised article has been evaluated by Christian Landry (Senior Editor) and a Reviewing Editor.

The manuscript has been improved but there are some remaining issues that need to be addressed, as outlined below:

The three reviewers appreciated all of the hard work and adjustments made to the manuscript. Overall, many of their comments can be addressed by additional explanations and addition of a few caveats. I have added short suggestions to the comments from each reviewer to help guide your edits.

Reviewer #2 (Recommendations for the authors):

In this revised version of their manuscript, Long et al. present further experimental evidence to support their claim that the peel-1 toxin, which is part of a paternal-effect toxin-antidote element in C. elegans, increases the competitive fitness of selfing hermaphrodites compared to those not carrying a copy. Several reviewers independently pointed out that to convincingly show this, the authors needed (1) to generate independent peel-1 knockout alleles that recapitulated the effect of the peel-1(kah126) mutant and (2) a rescue experiment, ideally a repair or reversion of the mutated allele back to WT to rule out any background effects. For this revision, the authors have generated additional strains and performed new competitive fitness assays to provide more convincing evidence that the fitness effect, albeit small, is indeed reproducible and caused by peel-1.

1. While the authors have addressed the major criticisms that focused on the genetics and reproducibility of the peel-1 mutant effect, there are some aspects of their fitness assays that remain unclear at the moment and would be important to clarify. The results shown in panel Figure 4D are central to the interpretation of the main claim of this paper, yet several questions come into mind upon close inspection, for instance:

1.1 Why is the data coming from independently generated alleles of the same genotype combined? Looking at the source data, it would appear that the authors replicated each pair-wise competition assay 6 times. However the data originating from independent alleles were combined in the final plots. As a result, the wt control and the original peel-1 mutant allele (kah126) have 6 replicates each, whereas other conditions, like the peel-1 "revertant" mutants and "new" peel-1 mutants have 12 and 18 replicates, respectively. I find it a bit troublesome that the fitness estimations are being done by aggregating independently derived lines (which goes against the original purpose of having independent alleles).

– The data for the different lines can be separated and reported.

1.2. Although it was brought up by a reviewer in the first round, it appears that there is no information available on the timing of the competitive fitness experiments. Were the experiments performed in parallel? And if not, when exactly? (this is important information for readers that should be available in the methods section/supplement).

– Please answer this question by adding text to the Methods.

2. I think it would be very important to check that the phenotype of the new peel-1 lines (new mutant alleles and revertant) is also consistent when measuring the total number of offspring laid by hermaphrodites (see Figure 3C)

– Without these data, the authors can mention that this trait was not measured for all of the peel-1 lines.

3. The authors may want to reconsider or justify the use of the term "biological role", for example as used in line 196

"These experiments strongly support a biological role for peel-1. "

I find the use of the term "biological role" very confusing in this context because it implies that the role of peel-1 as a toxin (or that of selfish elements in general) is "non- biological". Maybe the authors refer to a "physiological role" (not perfect either but more accurate)?

– Please edit to a different term. All genes have biological and physiological roles. Maybe "fitness-relevant role"?

Overall, this is a very exciting and interesting result and the manuscript has been greatly improved. Yet, many questions still remain open (which is OK if this is intended to be only a short report). How would a protein that is only expressed in sperm delay the development of hermaphrodites? Does this effect depend on zeel-1? Are the two opposing roles of peel-1 independent? (in other words, can one isolate mutants that abrogate toxicity but not the effect on fitness and vice versa). Does the benefit of carrying peel-1 evolved before or after the toxicity? Is there balancing selection and what is the selective force?

– Depending on space in the Discussion, some or all of these points can be addressed.