The manuscript entitled ‚A potential role for overdominance in the maintenance of color variation in the Neotropical tortoise beetle, Chelymorpha alternans‘ describes mate choice experiments in tortoise beetles, which indicate that females do not choose males based on their color. However, breeding experiments revealed that dissassortative matings resulted in offspring with higher viability but no larger clutch sizes. The authors thus speculate that the color polymorphism may be maintained by balancing selection due to overdominance. I overall enjoyed reading this manuscript and find this a very interesting system. However, I do have some conceptual concerns and would recommend to also discuss the potential role of sexual selection and other evolutionary mechanisms that may contribute to these patterns.

The authors mention that the polymorphism has a simple genetic basis and describe the genetics in the methods. However, I feel that the info on the genetic basis would better fit into the introduction where you introduce your system. I would also update Figure S1 and its figure legend since it is difficult to read this Figure without context. Moreover, it remains unclear if these color patterns differ among sexes? It not, this may speak against color as a trait under female (sexual) selection. Is anything known about that?

I am missing discussion on other potential evolutionary mechanisms that may lead to stable color polymorphisms. For example, the population samples compared here may experience strong and ongoing admixture from more distant pure-breed populations, which results in common non-adaptive hybridization and polymorphism at the sampling sites. Accordingly, I would like to read more about the geographic distribution of this species as a whole and more specifically of the different color morphs. Table S2 suggests that the distribution of color morphs only partially overlaps.

Why only one-directional crosses? Mate preference may be a function of female choice, i.e. when a female can choose between males (or males fight over a female). But males may also exhibit mate choice, i.e. in the presence of multiple females. It needs to be clearly justified why only female choice was tested here.

Minor comments

Lines 269. Perhaps I am misunderstanding, but isn’t the t-test somehow redundant to the ANOVA below? I would skip the t-test in this case and use planned contrasts to explicitly compare assortative and dissassortative cross types.

Lines 333 ff. I do not know if a detailed discussion of such different and distant systems is necessary here.

Lines 364. To which extend may the specific environmental conditions at the experimental site play a role in the offspring survival rates? If certain morphs are better adapted to different climates, the observed fitness patterns may rather reflect local adaptation (or the lack of it). However, your statement about the distribution of metallic morphs speaks against my hypothesis

Lines 404. I think it would be very easy (and worth it) to test for the presence for Wolbachia with universal PCR primers targeting the wsp gene (e.g. Zhou et al. 1989). Moreover, the intensity of cytoplasmic incompatibility (CI) is highly variable in several species. Thus, I would not conclude that the absence of complete or strong CI speaks against subtle effects of Wolbachia on fecundity and egg viability.

Page 33. This Figure lacks a number and a legend and is not (clearly) referenced in the MS.

References

Zhou, W., Rousset, F., & O'Neil, S. (1998). Phylogeny and PCR-based classification of Wolbachia strains using wsp gene sequences. Proceedings. Biological sciences, 265(1395), 509–515. https://doi.org/10.1098/rspb.1998.0324

After carefully re-reading the rebuttal letter and the revised manuscript, I find that the authors invested well in revising the manuscript in response of the reviewer’s comments. In particular, the study has benefitted from improved statistical analyses and a more thorough and detailed discussion.