Fast evolutionary turnover and overlapping variances of sex-biased gene expression patterns defy a simple binary classification of sexes

Reviewer #1 (Public Review):

The authors describe a comprehensive analysis of sex-biased expression across multiple tissues and species of mouse. Their results are broadly consistent with previous work, and their methods are robust, as the large volume of work in this area has converged toward a standardized approach.

I have a few quibbles with the findings, and the main novelty here is the rapid evolution of sex-biased expression over shorter evolutionary intervals than previously documented, although this is not statistically supported. The other main findings, detailed below, are somewhat overstated.

(1) In the introduction, the authors conflate gametic sex, which is indeed largely binary (with small sperm, large eggs, no intermediate gametic form, and no overlap in size) with somatic sexual dimorphism, which can be bimodal (though sometimes is even more complicated), with a large variance in either sex and generally with a great deal of overlap between males and females. A good appraisal of this distinction is at https://doi.org/10.1093/icb/icad113. This distinction in gene expression has been recognized for at least 20 years, with observations that sex-biased expression in the soma is far less than in the gonad.

For example, the authors frame their work with the following statement:
"The different organs show a large individual variation in sex-biased gene expression, making it impossible to classify individuals in simple binary terms. Hence, the seemingly strong conservation of binary sex-states does not find an equivalent underpinning when one looks at the gene-expression makeup of the sexes"

The authors use this conflation to set up a straw man argument, perhaps in part due to recent political discussions on this topic. They seem to be implying one of two things. a) That previous studies of sex-biased expression of the soma claim a binary classification. I know of no such claim, and many have clearly shown quite the opposite, particularly studies of intra-sexual variation, which are common - see https://doi.org/10.1093/molbev/msx293, https://doi.org/10.1371/journal.pgen.1003697, https://doi.org/10.1111/mec.14408, https://doi.org/10.1111/mec.13919, https://doi.org/10.1111/j.1558-5646.2010.01106.x for just a few examples. Or b) They are the first to observe this non-binary pattern for the soma, but again, many have observed this. For example, many have noted that reproductive or gonad transcriptome data cluster first by sex, but somatic tissue clusters first by species or tissue, then by sex (https://doi.org/10.1073/pnas.1501339112, https://doi.org/10.7554/eLife.67485)
Figure 4 illustrates the conceptual difference between bimodal and binary sexual conceptions. This figure makes it clear that males and females have different means, but in all cases the distributions are bimodal.

I would suggest that the authors heavily revise the paper with this more nuanced understanding of the literature and sex differences in their paper, and place their findings in the context of previous work.

(2) The authors also claim that "sexual conflict is one of the major drivers of evolutionary divergence already at the early species divergence level." However, making the connection between sex-biased genes and sexual conflict remains fraught. Although it is tempting to use sex-biased gene expression (or any form of phenotypic dimorphism) as an indicator of sexual conflict, resolved or not, as many have pointed out, one needs measures of sex-specific selection, ideally fitness, to make this case (https://doi.org/10.1086/595841, 10.1101/cshperspect.a017632). In many cases, sexual dimorphism can arise in one sex only without conflict (e.g. 10.1098/rspb.2010.2220). As such, sex-biased genes alone are not sufficient to discriminate between ongoing and resolved conflict.

(3) To make the case that sex-biased genes are under selection, the authors report alpha values in Figure 3B. Alpha value comparisons like this over large numbers of genes often have high variance. Are any of the values for male- female- and un-biased genes significantly different from one another? This is needed to make the claim of positive selection.

Reviewer #2 (Public Review):

The manuscript by Xie and colleagues presents transcriptomic experiments that measure gene expression in eight different tissues taken from adult female and male mice from four species. These data are used to make inferences regarding the evolution of sex-biased gene expression across these taxa. The experimental methods and data analysis are appropriate; however, most of the conclusions drawn in the manuscript have either been previously reported in the literature or are not fully supported by the data.

There are two ways the manuscript could be modified to better strengthen the conclusions.

First, some of the observed differences in gene expression have very little to no effect on other phenotypes, and are not relevant to medicine or fitness. Selectively neutral gene expression differences have been inferred in previous studies, and consistent with that work, sex-biased and between-species expression differences in this study may also be enriched for selectively neutral expression differences. This idea is supported by the analysis of expression variance, which indicates that genes that show sex-biased expression also tend to show more inter-individual variation. This perspective is also supported by the MK analysis of molecular evolution, which suggests that positive selection is more prevalent among genes that are sex-biased in both mus and dom, and genes that switch sex-biased expression are under less selection at the level of both protein-coding sequence and gene expression.

As an aside, I was confused by (line 176): "implying that the enhanced positive selection pressure is triggered by their status of being sex-biased in either taxon." - don't the MK values suggest an excess of positive selection on genes that are sex-biased in both taxa?

Without an estimate of the proportion of differentially expressed genes that might be relevant for broader physiological or organismal phenotypes, it is difficult to assess the accuracy and relevance of the manuscript's conclusions. One (crude) approach would be to analyze subsets of genes stratified by the magnitude of expression differences; while there is a weak relationship between expression differences and fitness effects, on average large gene expression differences are more likely to affect additional phenotypes than small expression differences. Another perspective would be to compare the within-species variance to the between-species variance to identify genes with an excess of the latter relative to the former (similar logic to an MK test of amino acid substitutions).

Second, the analysis could be more informative if it distinguished between genes that are expressed across multiple tissues in both sexes that may show greater expression in one sex than the other, versus genes with specialized function expressed solely in (usually) reproductive tissues of one sex (e.g. ovary-specific genes). One approach to quantify this distinction would be metrics like those used defined by [Yanai I, et al. 2005. Genome-wide midrange transcription profiles reveal expression-level relationships in human tissue specification. Bioinformatics 21:650-659.] These approaches can be used to separate out groups of genes by the extent to which they are expressed in both sexes versus genes that are primarily expressed in sex-specific tissue such as testes or ovaries. This more fine-grained analysis would also potentially inform the section describing the evolution/conservation of sex-biased expression: I expect there must be genes with conserved expression specifically in ovaries or testes (these are ancient animal structures!) but these may have been excluded by the requirement that genes be sex-biased and expressed in at least two organs.

There are at least three examples of statements in the discussion that at the moment misinterpret the experimental results.

The discussion frames the results in the context of sexual selection and sexually antagonistic selection, but these concepts are not synonymous. Sexual selection can shape phenotypes that are specific to one sex, causing no antagonism; and fitness differences between males and females resulting from sexually antagonistic variation in somatic phenotypes may not be acted on by sexual selection. Furthermore, the conditions promoting and consequence of both kinds of selection can be different, so they should be treated separately for the purposes of this discussion.

The discussion claims that "Our data show that sex-biased gene expression evolves extremely fast" but a comparison or expectation for the rate of evolution is not provided. Many other studies have used comparative transcriptomics to estimate rates of gene expression evolution between species, including mice; are the results here substantially and significantly different from those previous studies? Furthermore, the experimental design does not distinguish between those gene expression phenotypes that are fixed between species as compared to those that are polymorphic within one or more species which prevents straightforward interpretation of differences in gene expression as interspecific differences.

The conclusion that "Our results show that most of the genetic underpinnings of sex differences show no long-term evolutionary stability, which is in strong contrast to the perceived evolutionary stability of two sexes" - seems beyond the scope of this study. This manuscript does not address the genetic underpinnings of sex differences (this would involve eQTL or the like), rather it looks at sex differences in gene expression phenotypes. Simply addressing the question of phenotypic evolutionary stability would be more informative if genes expressed specifically in reproductive tissues were separated from somatic sex-biased genes to determine if they show similar patterns of expression evolution.

Reviewer #3 (Public Review):

This manuscript reports some interesting and important patterns. The results on sex-bias in different tissues and across four taxa would benefit from alternative (or additional) presentation styles. In my view, the most important results are with respect to alpha (fraction of beneficial amino acid changes) in relation to sex-bias (though the authors have made this as a somewhat minor point in this version).

The part that the authors emphasize I don't find very interesting (i.e., the sexes have overlapping expression profiles in many nongonadal tissues), nor do I believe they have the appropriate data necessary to convincingly demonstrate this (which would require multiple measures from the same individual).

This study reports several interesting patterns with respect to sex differences in gene expression across organs of four mice taxa. An alternative presentation of the data would yield a clearer and more convincing case that the patterns the authors claim are legitimate.

I recommend that the authors clarify what qualifies as "sex-bias".

Author response:

We appreciate the time of the reviewers and their detailed comments, which will help to improve the manuscript.

We are sorry that at least one reviewer seems to have had the impression that we have conflated issues about gonadal and non-gonadal sex phenotypes. This referee suggests that we should use Sharpe et al. (2023) to develop our concepts. However, what is discussed in Sharpe et al. was already the guiding principle for our study (without knowing this paper before). In our paper, we introduce the gonadal binary sex (which is self-evidently also the basis for creating the dataset in the first place, because we needed to separate males from females) and go then on to the question of (adult) sex phenotypes for the rest of the paper. The gonadal data are included only as comparison for contrasting the patterns in the non-gonadal tissues.

Our study presents the largest systematic dataset so far on the evolution of sex-biased gene expression. It is also the first that explores the patterns of individual variation in sex-biased gene expression and the SBI is an entirely new procedure to directly visualize these variance patterns in an intuitive way (note that the relative position of the distributions along the X-axis is indeed not relevant). The results are actually quite nuanced (e.g. the rather dynamv changes seen in mouse kidney and liver comparisons) and go certainly beyond what would have been predictable based on the current literature.

Also, we should like to point out that our study contradicts recent conclusions that were published in high profile journals, that had suggested that a substantial set of sex-biased genes has conserved functions between humans and mice and that mice can therefore be informative for gender-specific medicine studies. Our data suggest that that only a very small set of genes are conserved in their sex-biased expression. These are epigenetic regulator genes and it will therefore be interesting in the future to focus on their roles in generating the differences between sexual phenotypes in given species.

We will be happy to use the referee comments to clarify all of these points in a revised version. But we do not think that our "evidence is incomplete" and that there are several "overstated key conclusions". We have used all canonical statistical analyses that are typically used in papers of sex-biased gene expression, as acknowledged by reviewers 1 and 2. The additional statistical analyses that are requested are not within the scope of such papers, but could be subject to separate general studies, independent of the sex-bias analysis (e.g. the role of highly expressed genes versus low expressed genes, or the analysis of the fraction of neutrally evolving loci).

Finally, it is unclear why the overall rating of the paper is at the lowest possible category ("useful study"), given that it adds a substantial amount of data and new insights into the exploration of the non-binary nature of sexual phenotypes.