Alternative Splicing Across the Tree of Life: A Comparative Study

  1. Rebeca de la Fuente
  2. Wladimiro Díaz-Villanueva
  3. Vicente Arnau
  4. Andrés Moya

  • Curated by eLife

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    The authors examined the frequency of alternative splicing across prokaryotes and eukaryotes and found that the rate of alternative splicing varies with taxonomic groups and genome coding content. This solid work, based on nearly 1,500 high-quality genome assemblies, relies on a novel genome-scale metric that enables cross-species comparisons and that quantifies the extent to which coding sequences generate multiple mRNA transcripts via alternative splicing. This timely study provides an important basis for improving our general understanding of genome architecture and the evolution of life forms.

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Abstract

Abstract

There is a growing understanding of how alternative splicing contributes to functional specialization and adaptation, especially in well-studied model organisms. However, its large-scale evolutionary dynamics remain poorly understood. Through a comparative analysis of alternative splicing across 1,494 species spanning the entire tree of life, this study integrates numerous lines of prior evidence to provide a unified view of alternative splicing. We propose a novel genome-scale metric designed to support cross-species comparison. Our findings indicate that alternative splicing is highly variable across lineages. While unicellular eukaryotes and prokaryotes display minimal splicing, mammals and birds exhibit the highest levels of alternative splicing. Despite sharing a conserved intron-rich genomic architecture, mammals and birds show considerable interspecies divergence in splicing activity. In contrast, plants display moderate levels of alternative splicing but exhibit high variability of genomic composition. Furthermore, a strong negative correlation is observed between alternative splicing and the proportion of coding content in genes, with the highest levels of alternative splicing observed in genomes containing approximately 50% intergenic DNA.

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  1. eLife

    eLife Assessment

    The authors examined the frequency of alternative splicing across prokaryotes and eukaryotes and found that the rate of alternative splicing varies with taxonomic groups and genome coding content. This solid work, based on nearly 1,500 high-quality genome assemblies, relies on a novel genome-scale metric that enables cross-species comparisons and that quantifies the extent to which coding sequences generate multiple mRNA transcripts via alternative splicing. This timely study provides an important basis for improving our general understanding of genome architecture and the evolution of life forms.

  2. eLife

    Reviewer #2 (Public review):

    Summary:

    In this contribution, the authors investigate the degree of alternative splicing across the evolutionary tree, and identify a trend of increasing alternative splicing as you move from the base of the tree (here, only prokaryotes are considered) towards the tips of the tree. In particular, the authors investigate how the degree of alternative splicing (roughly speaking, the number of different proteins made from a single ORF (open reading frame) via alternative splicing) relates to three genomic variables: the genome size, the gene content (meaning the fraction of the genome composed of ORFs), and finally, the coding percentage of ORFs, meaning the ratio between exons and total DNA in the ORF.

    The revised manuscript addresses the problems identified in the first round of reviews and now serves as a guide to understand how alternative splicing has evolved within different phyla, as opposed to making unsubstantiated claims about overall trends.

  3. eLife

    Reviewer #3 (Public review):

    Summary:

    In "Alternative Splicing Across the Tree of Life: A Comparative Study," the authors use rich annotation features from nearly 1,500 high-quality NCBI genome assemblies to develop a novel genome-scale metric, the Alternative Splicing Ratio, that quantifies the extent to which coding sequences generate multiple mRNA transcripts via alternative splicing (AS). This standardized metric enables cross-species comparisons and reveals clear phylogenetic patterns: minimal AS in prokaryotes and unicellular eukaryotes, moderate AS in plants, and high AS in mammals and birds. The study finds a strong negative correlation between AS and coding content, with genomes containing approximately 50% intergenic DNA exhibiting the highest AS activity. By integrating diverse lines of prior evidence, the study offers a cohesive evolutionary framework for understanding how alternative splicing varies and evolves across the tree of life.

    Strengths:

    By studying alternative splicing patterns across the tree of life, the authors systematically address an important yet historically understudied driver of functional diversity, complexity, and evolutionary innovation. This manuscript makes a valuable contribution by leveraging standardized, publicly available genome annotations to perform a global survey of transcriptional diversity, revealing lineage-specific patterns and evolutionary correlates. The authors have done an admirable job in this revised version, thoroughly addressing prior reviewer comments. The updated manuscript includes more rigorous statistical analyses, careful consideration of potential methodological biases, expanded discussion of regulatory mechanisms, and acknowledgment of non-adaptive alternatives. Overall, the work presents an intriguing view of how alternative splicing may serve as a flexible evolutionary strategy, particularly in lineages with limited capacity for coding expansion (e.g., via gene duplication). Notably, the identification of genome size and genic coding fraction thresholds (~20 Mb and ~50%, respectively) as tipping points for increased splicing activity adds conceptual depth and potential generalizability.

    Weaknesses:

    While the manuscript offers a broad comparative view of alternative splicing, its central message becomes diffuse in the revised version. The focus of the study is unclear, and the manuscript comes across as largely descriptive without a well-articulated hypothesis or explanatory evolutionary model. Although the discussion gestures toward adaptive and non-adaptive mechanisms, these interpretations are not developed early or prominently enough to anchor the reader. The negative correlation between alternative splicing and coding content is compelling, but the biological significance of this pattern remains ambiguous: it is unclear whether it reflects functional constraint, genome organization, or annotation bias. This uncertainty weakens the manuscript's broader evolutionary inferences.

    Sections of the Introduction, particularly lines 72-90, lack cohesion and logical flow, shifting abruptly between topics without a clear structure. A more effective approach may involve separating discussions of coding and non-coding sequence evolution to clarify their distinct contributions to splicing complexity. Furthermore, some interpretive claims lack nuance. For example, the assertion that splicing in plants "evolved independently" seems overstated given the available evidence, and the citation regarding slower evolution of highly expressed genes overlooks counterexamples from the immunity and reproductive gene literature.

    Presentation of the results is occasionally vague. For instance, stating "we conducted comparisons of mean values" (line 146) without specifying the metric undercuts interpretability. The authors should clarify whether these comparisons refer to the Alternative Splicing Ratio or another measure. Additionally, the lack of correlation between splicing and coding region fraction in prokaryotes may reflect a statistical power issue, particularly given their limited number of annotated isoforms, rather than a biological absence of pattern.

    Finally, the assessment of annotation-related bias warrants greater methodological clarity. The authors note that annotations with stronger experimental support yield higher splicing estimates, yet the normalization strategy for variation in transcriptomic sampling (e.g., tissue breadth vs sequencing depth) is insufficiently described. As these factors can significantly influence splicing estimates, a more rigorous treatment is essential. While the authors rightly acknowledge that splicing represents only one layer of regulatory complexity, the manuscript would benefit from a more integrated consideration of additional dimensions, such as 3D genome architecture, e.g., the potential role of topologically associating domains in constraining splicing variation.

  4. eLife

    Reviewer #4 (Public review):

    The manuscript reports on a large-scale study correlating genomic architecture with splicing complexity over almost 1,500 species. We still know relatively little about alternative splicing functional consequences and evolution, and thus, the study is relevant and timely. The methodology relies on annotations from NCBI for high-quality genomes and a main metric proposed by the authors and named Alternative Splicing Ratio (ASR). It quantifies the level of redundancy of each coding nucleotide in the annotated isoforms.

    According to the authors' response to the first reviewers' comments, the present version of the manuscript seems to be a profoundly revised version compared to the original submission. I did not have access to the reviewers' comments.

    Although the study addresses an important question and the authors have visibly made an important effort to make their claims more statistically robust, I have a number of major concerns regarding the methodology and its presentation.

    (1) A large part of the manuscript is speculative and vague. For instance, the Discussion is very long (almost longer than the Results section) and the items discussed are sometimes not in direct connection with the present work. I would suggest merging the last 2 paragraphs, for instance, since the before last paragraph is essentially a review of the literature without direct connection to the present work.

    (2) The Methods section lacks clarity and precision. A large part is devoted to explaining the biases in the data without any reference or quantification. The definition of ASR is very confusing. It is first defined in equation 2, with a different name, and then again in the next subsection from a different perspective on lines 512-518. Why build matrices of co-occurrences if these are, in practice, never used? It seems the authors exploit only the trace. A major revision, if I understood correctly, was the correction/normalisation of the ASR metric. This normalisation is not explained. The authors argue that they will write another paper about it, I do not think this is acceptable for the publication of the present manuscript. Furthermore, there is no information about the technical details of the implementation: which packages did the authors use?

    (3) Could the authors motivate why they do not directly focus on the MC permutation test? They motivate the use of permutations because the data contains extreme outliers and are non normal in most cases. Hence, it seems the Welch's ANOVA is not adapted. "To further validate our findings, we also conducted
    148 a Monte Carlo permutation test, which supported the conclusions (see Methods)." Where is the comparison shown? I did not see any report of the results for the non-permuted version of the Welch's ANOVA.

    (4) What are the assumptions for the Phylogenetic Generalized Least Squares? Which evolution model was chosen and why? What is the impact of changing the model? Could the authors define more precisely (e.g. with equations) what is lambda? Is it estimated or fixed?

    (5) I think the authors could improve their account of recent literature on the topic. For instance, the paper https://doi.org/10.7554/eLife.93629.3, published in the same journal last year, should be discussed. It perfectly fits in the scope of the subsection "Evidence for the adaptive role of alternative splicing". Methods and findings reported in https://doi.org/10.1186/s13059-021-02441-9 and https://www.genome.org/cgi/doi/10.1101/gr.274696.120 directly concern the assessment of AS evolutionary conservation across long evolutionary times and/or across many species. These aspects are mentioned in the introduction on p.3. but without pointing to such works. Can we really qualify a work published in 2011 as "recent" (line 348-350)?

    The generated data and codes are available on Zenodo, which is a good point for reproducibility and knowledge sharing with the community.

  5. eLife

    Author response:

    The following is the authors’ response to the original reviews.

    Reviewer #1

    Methodological biases in annotation and sequencing methods

    We acknowledge the reviewer’s concern regarding methodological heterogeneity in genome annotations, particularly regarding the use of CDS annotations derived from public databases. In response, we have properly addressed the potential sources of bias in estimating alternative splicing (AS) across such a broad taxonomic range.

    Given the methodological challenges encountered in this study, we have undertaken an in-depth analysis of the biases associated with genome annotations and their impact on large-scale estimates of alternative splicing. This effort has resulted in the development of a comprehensive framework for quantifying, modeling, and correcting such biases, which we believe will be of interest to the broader genomics community. We are currently preparing a separate manuscript dedicated to this methodological aspect, which we intend to submit for publication in the near future.

    To account for these biases, we performed a statistical evaluation of annotation quality by examining the relationship between ASR values and multiple features of the NCBI annotation pipeline, including both technical and biological variables. Specifically, we analyzed a set of metadata descriptors related to: (i) genome assembly quality (e.g., Contig N50, Scaffold N50, number of gaps, gap length, contig/scaffold count), (ii) the amount and diversity of experimental evidence used in annotation (e.g., number of RNA-Seq reads, number of tissues, number of experimental runs, number of proteins and transcripts, including those derived from Homo sapiens), and (iii) the nature of the annotated coding sequences (e.g., total number of CDSs, percentage of CDSs supported by experimental evidence, proportion of known CDSs, percentage of CDSs derived from ab initio predictions).

    This comprehensive analysis revealed that the strongest bias affecting ASR values is associated with the proportion of fully supported CDSs, which showed a strong positive correlation with observed splicing levels. In contrast, the percentage of CDSs relying on ab initio models showed a negative correlation, indicating that computational predictions tend to underestimate splicing complexity. Based on these findings, we implemented a polynomial normalization model using the percentage of fully supported CDSs as the main predictor of annotation bias. The resulting normalized metric, ASR∗, corrects for annotation-related variability while preserving biologically meaningful variation.

    We further verified the robustness of this correction by comparing the main results of our study using both the raw ASR and the normalized ASR* across all analyses. The qualitative and quantitative consistency of results obtained with both metrics demonstrates that our findings are not an artifact of methodological bias and validates the reliability of our approach.

    Conceptual and Statistical Framework

    Our aim was not to investigate specific regulatory mechanisms of alternative splicing, but rather to explore large-scale statistical patterns across the tree of life using a newly defined metric—the Alternative Splicing Ratio (ASR)—that enables genome-wide comparisons of splicing complexity across species. To clarify the conceptual framework, we have revised the manuscript to explicitly state our assumptions, objectives, and the scope of our conclusions. The ASR metric is now briefly introduced in the Results section, with a more detailed mathematical formulation included in the Methods section.

    From a methodological standpoint, we have expanded the manuscript to better support the comparative framework through additional statistical analyses. In particular, we now include:

    • Monte Carlo permutation tests to assess pairwise differences in splicing and genomic variables across taxonomic groups, which are robust to non-normality and heteroscedasticity in the data.

    • Welch’s ANOVA with Bonferroni correction, which accounts for unequal variances when comparing group means.

    • Phylogenetic Generalized Least Squares (PGLS) regression, which explicitly models phylogenetic non-independence between species and allows us to infer lineage-specific associations between genomic composition and alternative splicing.

    • Coefficient of variation analysis, used to evaluate the relative variability of splicing and genomic traits across groups in a scale-independent manner.

    • Variability ratio metrics, designed to compare the dispersion of splicing values relative to genomic features, thereby quantifying trends in regulatory plasticity versus structural constraints.

    All methods are thoroughly described in the revised Methods section, and their application is presented in the Results section.

    Functional vs. non-functional nature of AS events

    We have included a new discussion paragraph addressing the ongoing debate regarding the functionality of alternative splicing and a possible non-adaptive explanation for the patterns observed. While many previous studies suggest that a considerable fraction of AS events might represent splicing noise or non-functional isoforms, our intention is not to adopt this view uncritically. Instead, we cite recent literature to provide a more nuanced interpretation, recognizing both the potential adaptive value and the uncertainty surrounding the functional relevance of many AS events. Thus, rather than assuming that all observed alternative splicing events are adaptive or biologically meaningful, we now emphasize that many patterns may emerge from other processes, such as those associated to genomic constraints.

    Terminology and Result Interpretation

    The manuscript has been thoroughly revised to improve both the scientific language and the conceptual framing. We have removed inappropriate terminology such as “higher/lower organisms” and “highly evolved”. Also, we have reinterpreted the results. As part of this process, the manuscript has been substantially rewritten to focus on the most meaningful findings. Ultimately, we have retained only those results that specifically concern broad-scale patterns of alternative splicing across taxa, which are now presented with greater clarity and methodological rigor.

    Reviewer #2

    Gene Regulatory Complexity Beyond Splicing Mechanisms

    While alternative splicing represents a prominent mechanism of transcriptomic diversification, we agree with the reviewer that it constitutes only one component of the broader landscape of gene regulation. Structural and behavioral complexity in organisms arises from a combination of regulatory processes, and our study focuses specifically on alternative splicing as a measurable proxy within this multifactorial system. To clarify this point, we have added a paragraph in the Discussion section, where we explicitly contextualize alternative splicing within the wider regulatory architecture. In that paragraph, we discuss additional mechanisms that contribute to phenotypic complexity—such as transcriptional control, chromatin remodeling, epigenetic modifications, and RNA editing—citing key literature.

    Alternative Splicing Measure and Methodology

    While we agree that alternative splicing is not a definitive measure of organismal complexity, we argue that it remains a meaningful proxy for transcriptomic and regulatory diversification, especially when analyzed at large phylogenetic scale. In this version of the manuscript, our goal was not to equate alternative splicing with biological complexity, but rather to quantify its patterns across lineages and evaluate its relationship with genome structure. This point is now explicitly stated in both the Introduction and Discussion.

    We also recognize the limitations associated with the use of coding sequence (CDS) annotations from public databases such as NCBI RefSeq. To address this concern, we have conducted a detailed analysis of the potential biases introduced by heterogeneous annotation quality, sequencing depth, and computational prediction, as previously addressed in our response to Reviewer #1.

    In response to concerns about unsupported statements, we have completely rewritten the manuscript to ensure that all claims are now explicitly supported by data and grounded in up-to-date scientific literature. We have reformulated speculative statements, removed inappropriate generalizations, and improved the logical flow of the arguments throughout the text. In summary, we have strengthened both the conceptual framework and the methodological foundation of the study, while maintaining a cautious interpretation of the results.

    Trends of Alternative Splicing

    To address the reviewer’s concern, we have revised the interpretation of trends as used in our analysis. In this study, we define a trend not as a strict directional progression or a linear trajectory across all species, but rather as a broad statistical pattern observable in the relative distribution and variability of alternative splicing across major taxonomic groups. We do not claim that this pattern reflects a universal adaptive pathway. Instead, we interpret it as a signal of differences in regulatory strategies associated to the genome architecture. To avoid misinterpretation, we have rephrased several sentences in the manuscript and explicitly emphasized the variability within groups, and the lack of significant correlations in certain clades.

    Inconsistent statistics

    The discrepancies pointed out were due to differences between mean and median-based analyses. These have been clarified and consistently reported in the revised manuscript. Error bars, p-values, and a supplementary table summarizing all tests are now included. Furthremore, we have no removed any species from our dataset.

  6. Version published to 10.7554/elife.94802.2 on eLife
  7. Version published to 10.7554/elife.94802 on eLife
  8. Version published to 10.7554/elife.94802.1 on eLife
  10. eLife

    Author response:

    Reviewer #1 (Public Review):

    Summary:

    The authors collected genomic information from public sources covering 423 eukaryote genomes and around 650 prokaryote genomes. Based on pre-computed CDS annotation, they estimated the frequency of alternative splicing (AS) as a single average measure for each genome and computed correlations with this measure and other genomic properties such as genome size, percentage of coding DNA, gene and intergenic span, etc. They conclude that AS frequency increases with genome complexity in a somewhat directional trend from "lower" organisms to "higher" organisms.

    Strengths:

    The study covers a wide range of taxonomic groups, both in prokaryotes and eukaryotes.

    Weaknesses:

    The study is weak both methodologically and conceptually. Current high throughput sequencing technologies, coupled with highly heterogeneous annotation methods, can observe cases of AS with great sensitivity, and one should be extremely cautious of the biases and rates of false positives associated with these methods. These issues are not addressed in the manuscript. Here, AS measures seem to be derived directly from CDS annotations downloaded from public databases, and do not account for differing annotation methods or RNA sequencing depth and tissue sample diversity.

    We are aware of the bias that may exist in annotation files. Since the source of noise can be highly variable, we have assumed that most of the data has a similar bias. However, we agree with the reviewer that we could perform some analysis to test for these biases and their association to different methodologies. Thus, we will measure the uncertainty present in the data. From one side, we will be more explicit about the data limitations and the biases it can generate in the results. On the other side, while analyzing the false positives in the data is out of our scope, we will perform a statistical test to detect possible biases regarding different methods of sequencing and annotation, and types of organisms (model or non-model organisms). If positive, we will proceed, as far as possible, to normalize the data or to estimate a confidence interval.

    Here, AS measures seem to be derived directly from CDS annotations downloaded from public databases, and do not account for differing annotation methods or RNA sequencing depth and tissue sample diversity.

    Beyond taking into account the differential bias that may exist in the data, we do not consider that our AS measure is problematic. The NCBI database is one of the most reliable databases that we have to date and is continuously updated from all scientific community. So, the use of this data and the corresponding procedures for deriving the AS measure are perfectly acceptable for a comparative analysis on such a huge global scale. Furthermore, the proposal of a new genome-level measure of AS that allows to compare species spanning the whole tree of life is part of the novelty of the study. We understand that small-scale studies require a high specificity about the molecular processes involved in the study. However, this is not the case, where we are dealing with a large-scale problem. On the other side, as we have previously mention, we agree with the reviewer to analyze the degree of uncertainty in the data to better interpret the results.

    There is no mention of the possibility that AS could be largely caused by random splicing errors, a possibility that could very well fit with the manuscript's data. Instead, the authors adopt early on the view that AS is regulated and functional, generally citing outdated literature.

    There is no question that some AS events are functional, as evidenced by strongly supported studies. However, whether all AS events are functional is questionable, and the relative fractions of functional and non-functional AS are unknown. With this in mind, the authors should be more cautious in interpreting their data.

    Many studies suggest that most of the AS events observed are the result of splicing errors and are therefore neither functional nor conserved. However, we still have limited knowledge about the functionality of AS. Just because we don’t have a complete understanding of its functionality, doesn’t mean there isn’t a fundamental cause behind these events. AS is a highly dynamic process that can be associated with processes of a stochastic nature that are fundamental for phenotypic diversity and innovation. This is one of the reasons why we do not get into a discussion about the functionality of AS and consider it as a potential measure of biological innovation. Nevertheless, we agree with the reviewer’s comments, so we will add a discussion about this issue with updated literature and look at any possible misinterpretation of the results.

    The "complexity" of organisms also correlates well (negatively) with effective population size. The power of selection to eliminate (slightly) deleterious mutations or errors decreases with effective population size. The correlation observed by the authors could thus easily be explained by a non-adaptive interpretation based on simple population genetics principles.

    We appreciate the observation of the reviewer. We know well the M. Lynch’s theory on the role of the effective population size and its eventual correlation with genomic parameters, but we want to emphasize that our objective is not to find an adaptive or non-adaptive explanation of the evolution of AS, but rather to reveal it. Nevertheless, as the reviewer suggests, we will look at the correlation between the AS and the effective population size and discuss about a possible non-adaptive interpretation.

    The manuscript contains evidence that the authors might benefit from adopting a more modern view of how evolution proceeds. Sentences such as "... suggests that only sophisticated organisms optimize alternative splicing by increasing..." (L113), or "especially in highly evolved groups such as mammals" (L130), or the repeated use of "higher" and "lower" organisms need revising.

    As the reviewer suggests, we will proceed with the corresponding linguistic corrections.

    Because of the lack of controls mentioned above, and because of the absence of discussion regarding an alternative non-adaptive interpretation, the analyses presented in the manuscript are of very limited use to other researchers in the field. In conclusion, the study does not present solid conclusions.

    Reviewer #2 (Public Review):

    Summary:

    In this contribution, the authors investigate the degree of alternative splicing across the evolutionary tree and identify a trend of increasing alternative splicing as you move from the base of the tree (here, only prokaryotes are considered) towards the tips of the tree. In particular, the authors investigate how the degree of alternative splicing (roughly speaking, the number of different proteins made from a single ORF (open reading frame) via alternative splicing) relates to three genomic variables: the genome size, the gene content (meaning the fraction of the genome composed of ORFs), and finally, the coding percentage of ORFs, meaning the ratio between exons and total DNA in the ORF. When correlating the degree of alternative splicing with these three variables, they find that the different taxonomic groups have a different correlation coefficient, and identify a "progressive pattern" among metazoan groups, namely that the correlation coefficient mostly increases when moving from flowering plants to arthropods, fish, birds, and finally mammals. They conclude that therefore the amount of splicing that is performed by an organismal group could be used as a measure of its complexity.

    Weaknesses:

    While I find the analysis of alternative splicing interesting, I also find that it is a very imperfect measure of organismal complexity and that the manuscript as a whole is filled with unsupported statements. First, I think it is clear to anyone studying evolution over the tree of life that it is the complexity of gene regulation that is at the origin of much of organismal structural and behavioral complexity. Arguably, creating different isoforms out of a single ORF is just one example of complex gene regulation. However, the complexity of gene regulation is barely mentioned by the authors.

    We disagree with the reviewer with that our measure of AS is imperfect. Just as we responded to the first reviewer, we will quantify the uncertainty in the data and correct for differential biases caused by annotation and sequencing methods. Thus, beyond correcting relevant biases in the data, we consider that our measure is adequate for a comparative analysis at a global scale. A novelty of our study is the proposal of a genome-level measure of AS that takes into account data from the entire scientific community.

    We want also to emphasize that we assume from the beginning that AS may reflect some kind of biological complexity, it is not a conclusion from the results. An argument in favor of such an assumption is that AS is associated with stochastic processes that are fundamental for phenotypic diversity and innovation. Of course, we agree with the reviewer that it is not the only mechanism behind biological complexity, so we will emphasize it in the manuscript. On the other side, we will be more explicit about the assumptions and objectives, and will correct any unsupported statement.

    Further, it is clear that none of their correlation coefficients actually show a simple trend (see Table 3). According to these coefficients, birds are more complex than mammals for 3 out of 4 measures.

    An evolutionary trend is broadly defined as the gradual change in some characteristic of organisms as they evolve or adapt to a specific environment. Under our context, we define an evolutionary trend as the gradual change in genome composition and its association with AS across the main taxonomic groups. If we look at Figure 4 and Table 3 we can conclude that there is a progressive trend. We will be more precise about how we define an evolutionary trend and correct any possible misinterpretation of the results. On the other side, we do not assume that mammals should be more complex than birds. First, we will emphasize that our results show that birds have the highest values of such a trend. Second, after reading the reviewer’s comments, we have decided that we will perform an additional analysis to correct for differences in the taxonomic group sizes, which will allow us to have more confidence in the results.

    It is also not clear why the correlation coefficient between alternative splicing ratio and genome length, gene content, and coding percentage should display such a trend, rather than the absolute value. There are only vague mechanistic arguments.

    The study analyzes the relationship of AS with genomic composition for the large taxonomic groups. We assume that significant differences in these relationships are indicators of the presence of different mechanisms of genome evolution. However, we agree with the reviewer that a correlation does not imply a causal relation, so we will be more cautious when interpreting the results.

    To quantify the relationships we use correlation coefficients, the slopes of such correlations, and the relation of variability. Although the absolute values of AS are also illustrated in Table 4, we consider that they are less informative than if we include how it relates to the genomic composition. For example, we observe that plants have a different genome composition and relation with AS if compared to animals, which suggest that they follow different mechanisms of genome evolution. On the other hand, we observe a trend in animals, where high values of AS are associated to a large percentage of introns and a percentage of intergenic DNA of about the 50% of genomes.

    Much more troubling, however, is the statement that the data supports "lineage-specific trends" (lines 299-300). Either this is just an ambiguous formulation, or the authors claim that you can see trends *within* lineages.

    We agree with the reviewer that this statement is not correct, so we will proceed to correct it.

    The latter is clearly not the case. In fact, within each lineage, there is a tremendous amount of variation, to such an extent that many of the coefficients given in Table 3 are close to meaningless. Note that no error bars or p-values are presented for the values shown in Table 3. Figure 2 shows the actual correlation, and the coefficient for flowering plants there is given as 0.151, with a p-value of 0.193. Table 3 seems to quote r=0.174 instead. It should be clear that a correlation within a lineage or species is not a sign of a trend.

    The reviewer is not understanding correctly the results in Table 3. It is precisely the variation of the genome variables what we are measuring. Given the standardization of these values by the mean values, we have proceeded to compare the variability between groups, which is the result shown in Table 3. In this case there are no error bars or p-values associated. On the other hand, we agree that a correlation is not a sign of a trend. But the relations of variability, together with the results obtained in Figure 3, are indicators of a trend. As we mentioned before, we will proceed to analyze whether the variation in the group sizes is causing a bias in the results.

    There are several wrong or unsupported statements in the manuscript. Early on, the authors state that the alternative splicing ratio (a number greater or equal to one that can be roughly understood as the number of different isoforms per ORF) "quantifies the number of different isoforms that can be transcribed using the same amount of information" (lines 51-52). But in many cases, this is incorrect, because the same sequence can represent different amounts of information depending on the context. So, if a changed context gives rise to a different alternative splice, it is because the genetic sequence has a different meaning in the changed context: the information has changed.

    We agree that there are not well supported statements, so we will proceed to revise them.

    In line 149, the authors state that "the energetic cost of having large genomes is high". No citation is given, and while such a statement seems logical, it does not have very solid support.

    We will also revise the bibliography and support our statements with updated references.

    If there was indeed a strong selective force to reduce genome size, we would not see the stunning diversity of genome sizes even within lineages. This statement is repeated (without support) several times in the manuscript, apparently in support of the idea that mammals had "no choice" to increase complexity via alternative splicing because they can't increase it by having longer genomes. I don't think this reasoning can be supported.

    We agree with the reviewer in this issue, so we will carefully revise the statements that indirectly (or directly) assume the action of selective forces on the genome composition.

    Even more problematic is the statement that "the amount of protein-coding DNA seems to be limited to a size of about 10MB" (line 219). There is no evidence whatsoever for this statement.

    In Figure 1A we observe a one-to-one relationship between the genome size and the amount of coding. However, in multicellular organisms, although the genome size increases we observe that the amount of coding does not increase by more than 10Mb, which suggest the presence of some genomic limitation. Of course, this is not an absolute or general statement, but rather a suggestion. We are only describing our results.

    The reference that is cited (Choi et al 2020) suggests that there is a maximum of 150GB in total genome size due to physiological constraints. In lines 257-258, the authors write that "plants are less restricted in terms of storing DNA sequences compared to animals" (without providing evidence or a citation).

    We will revise the bibliography and add updated references.

    I believe this statement is made due to the observation that plants tend to have large intergenic regions. But without examining the functionality of these interagency regions (they might host long non-coding RNA stretches that are used to regulate the expression of other genes, for example) it is quite adventurous to use such a simple measure as being evidence that plants "are less restricted in terms of storing DNA sequences", whatever that even means. I do not think the authors mean that plants have better access to -80 freezers. The authors conclude that "plant's primary mechanism of genome evolution is by expanding their genome". This statement itself is empty: we know that plants are prone to whole genome duplication, but this duplication is not, as far as we understand, contributing to complexity. It is not a "primary mechanism of genome evolution".

    We will revise these statements.

    In lines 293-294, the authors claim that "alternative splicing is maximized in mammalian genomes". There is no evidence that this ratio cannot be increased. So, to conclude (on lines 302-303) that alternative splicing ratios are "a potential candidate to quantify organismal complexity" seems, based on this evidence, both far-fetched and weak at the same time.

    Our results show the highest values of AS in mammals, but we understand that the results are limited to the availability and accuracy of data, which we will emphasize in the manuscript. As we previously mention, we will also proceed to analyze the uncertainty in data and carry out the appropriate corrections.

    I am also not very comfortable with the data analysis. The authors, for example, say that they have eliminated from their analysis a number of "outlier species". They mention one: Emmer wheat because it has a genome size of 900 Mb (line 367). Since 900MB does not appear to be extreme, perhaps the authors meant to write 900 Gb. When I consulted the paper that sequenced Triticum dicoccoides, they noted that 14 chromosomes are about 10GB. Even a tetraploid species would then not be near 900Gb. But more importantly, such a study needs to state precisely which species were left out, and what the criteria are for leaving out data, lest they be accused of selecting data to fit their hypothesis.

    The reviewer is right, we wanted to say 900Mb, which is approximately 7.2Gb. We had a mistake of nomenclature. This value is extreme compared to the typical values, so it generates large deviations when applying measures of central tendency and dispersion. We want to obtain mean values that are representative of the most species composing the taxonomic groups, so we find appropriate to exclude all outlier values in the study. Nevertheless, we will specify the criteria that we have used to select the data in a rigorous way.

    I understand that Methods are often put at the end of a manuscript, but the measures discussed here are so fundamental to the analysis that a brief description of what the different measures are (in particular, the "alternative splicing ratio") should be in the main text, even when the mathematical definition can remain in the Methods.

    We agree with the reviewer, so we will add a brief description of the genomic variables at the beginning of the Results section.

    Finally, a few words on presentation. I understand that the following comments might read differently after the authors change their presentation. This manuscript was at the border of being comprehensible. In many cases, I could discern the meaning of words and sentences in contexts but sometimes even that failed (as an example above, about "species-specific trends", illustrates). The authors introduced jargon that does not have any meaning in the English language, and they do this over and over again.

    Note that I completely agree with all the comments by the other reviewer, who alerted me to problems I did not catch, including the possible correlation with effective population size: a possible non-adaptive explanation for the results.

  12. eLife

    eLife assessment

    The authors examined whether the frequency of alternative splicing across entire genomes correlates with measures of complexities across prokaryotes and eukaryotes. Although the question is very interesting and important for our general understanding of the evolution of life forms, the work is inadequate: the methods, data, and analyses do not support the primary claims. The measure of alternative splicing frequency used by the authors is problematic; the method is inappropriate; the observed correlations may also be explained by known population genetics principles; and parts of the manuscript are difficult to understand.

  13. eLife

    Reviewer #1 (Public Review):

    Summary:

    The authors collected genomic information from public sources covering 423 eukaryote genomes and around 650 prokaryote genomes. Based on pre-computed CDS annotation, they estimated the frequency of alternative splicing (AS) as a single average measure for each genome and computed correlations with this measure and other genomic properties such as genome size, percentage of coding DNA, gene and intergenic span, etc. They conclude that AS frequency increases with genome complexity in a somewhat directional trend from "lower" organisms to "higher" organisms.

    Strengths:

    The study covers a wide range of taxonomic groups, both in prokaryotes and eukaryotes.

    Weaknesses:

    The study is weak both methodologically and conceptually. Current high throughput sequencing technologies, coupled with highly heterogeneous annotation methods, can observe cases of AS with great sensitivity, and one should be extremely cautious of the biases and rates of false positives associated with these methods. These issues are not addressed in the manuscript. Here, AS measures seem to be derived directly from CDS annotations downloaded from public databases, and do not account for differing annotation methods or RNA sequencing depth and tissue sample diversity.

    There is no mention of the possibility that AS could be largely caused by random splicing errors, a possibility that could very well fit with the manuscript's data. Instead, the authors adopt early on the view that AS is regulated and functional, generally citing outdated literature.

    There is no question that some AS events are functional, as evidenced by strongly supported studies. However, whether all AS events are functional is questionable, and the relative fractions of functional and non-functional AS are unknown. With this in mind, the authors should be more cautious in interpreting their data. The "complexity" of organisms also correlates well (negatively) with effective population size. The power of selection to eliminate (slightly) deleterious mutations or errors decreases with effective population size. The correlation observed by the authors could thus easily be explained by a non-adaptive interpretation based on simple population genetics principles.

    The manuscript contains evidence that the authors might benefit from adopting a more modern view of how evolution proceeds. Sentences such as "... suggests that only sophisticated organisms optimize alternative splicing by increasing..." (L113), or "especially in highly evolved groups such as mammals" (L130), or the repeated use of "higher" and "lower" organisms need revising.

    Because of the lack of controls mentioned above, and because of the absence of discussion regarding an alternative non-adaptive interpretation, the analyses presented in the manuscript are of very limited use to other researchers in the field. In conclusion, the study does not present solid conclusions.

  14. eLife

    Reviewer #2 (Public Review):

    Summary:

    In this contribution, the authors investigate the degree of alternative splicing across the evolutionary tree and identify a trend of increasing alternative splicing as you move from the base of the tree (here, only prokaryotes are considered) towards the tips of the tree. In particular, the authors investigate how the degree of alternative splicing (roughly speaking, the number of different proteins made from a single ORF (open reading frame) via alternative splicing) relates to three genomic variables: the genome size, the gene content (meaning the fraction of the genome composed of ORFs), and finally, the coding percentage of ORFs, meaning the ratio between exons and total DNA in the ORF. When correlating the degree of alternative splicing with these three variables, they find that the different taxonomic groups have a different correlation coefficient, and identify a "progressive pattern" among metazoan groups, namely that the correlation coefficient mostly increases when moving from flowering plants to arthropods, fish, birds, and finally mammals. They conclude that therefore the amount of splicing that is performed by an organismal group could be used as a measure of its complexity.

    Weaknesses:

    While I find the analysis of alternative splicing interesting, I also find that it is a very imperfect measure of organismal complexity and that the manuscript as a whole is filled with unsupported statements. First, I think it is clear to anyone studying evolution over the tree of life that it is the complexity of gene regulation that is at the origin of much of organismal structural and behavioral complexity. Arguably, creating different isoforms out of a single ORF is just one example of complex gene regulation. However, the complexity of gene regulation is barely mentioned by the authors. Further, it is clear that none of their correlation coefficients actually show a simple trend (see Table 3). According to these coefficients, birds are more complex than mammals for 3 out of 4 measures. It is also not clear why the correlation coefficient between alternative splicing ratio and genome length, gene content, and coding percentage should display such a trend, rather than the absolute value. There are only vague mechanistic arguments.

    Much more troubling, however, is the statement that the data supports "lineage-specific trends" (lines 299-300). Either this is just an ambiguous formulation, or the authors claim that you can see trends *within* lineages. The latter is clearly not the case. In fact, within each lineage, there is a tremendous amount of variation, to such an extent that many of the coefficients given in Table 3 are close to meaningless. Note that no error bars or p-values are presented for the values shown in Table 3. Figure 2 shows the actual correlation, and the coefficient for flowering plants there is given as 0.151, with a p-value of 0.193. Table 3 seems to quote r=0.174 instead. It should be clear that a correlation within a lineage or species is not a sign of a trend.

    There are several wrong or unsupported statements in the manuscript. Early on, the authors state that the alternative splicing ratio (a number greater or equal to one that can be roughly understood as the number of different isoforms per ORF) "quantifies the number of different isoforms that can be transcribed using the same amount of information" (lines 51-52). But in many cases, this is incorrect, because the same sequence can represent different amounts of information depending on the context. So, if a changed context gives rise to a different alternative splice, it is because the genetic sequence has a different meaning in the changed context: the information has changed. In line 149, the authors state that "the energetic cost of having large genomes is high". No citation is given, and while such a statement seems logical, it does not have very solid support. If there was indeed a strong selective force to reduce genome size, we would not see the stunning diversity of genome sizes even within lineages. This statement is repeated (without support) several times in the manuscript, apparently in support of the idea that mammals had "no choice" to increase complexity via alternative splicing because they can't increase it by having longer genomes. I don't think this reasoning can be supported. Even more problematic is the statement that "the amount of protein-coding DNA seems to be limited to a size of about 10MB" (line 219). There is no evidence whatsoever for this statement. The reference that is cited (Choi et al 2020) suggests that there is a maximum of 150GB in total genome size due to physiological constraints. In lines 257-258, the authors write that "plants are less restricted in terms of storing DNA sequences compared to animals" (without providing evidence or a citation). I believe this statement is made due to the observation that plants tend to have large intergenic regions. But without examining the functionality of these interagency regions (they might host long non-coding RNA stretches that are used to regulate the expression of other genes, for example) it is quite adventurous to use such a simple measure as being evidence that plants "are less restricted in terms of storing DNA sequences", whatever that even means. I do not think the authors mean that plants have better access to -80 freezers. The authors conclude that "plant's primary mechanism of genome evolution is by expanding their genome". This statement itself is empty: we know that plants are prone to whole genome duplication, but this duplication is not, as far as we understand, contributing to complexity. It is not a "primary mechanism of genome evolution". In lines 293-294, the authors claim that "alternative splicing is maximized in mammalian genomes". There is no evidence that this ratio cannot be increased. So, to conclude (on lines 302-303) that alternative splicing ratios are "a potential candidate to quantify organismal complexity" seems, based on this evidence, both far-fetched and weak at the same time.

    I am also not very comfortable with the data analysis. The authors, for example, say that they have eliminated from their analysis a number of "outlier species". They mention one: Emmer wheat because it has a genome size of 900 Mb (line 367). Since 900MB does not appear to be extreme, perhaps the authors meant to write 900 Gb. When I consulted the paper that sequenced Triticum dicoccoides, they noted that 14 chromosomes are about 10GB. Even a tetraploid species would then not be near 900Gb. But more importantly, such a study needs to state precisely which species were left out, and what the criteria are for leaving out data, lest they be accused of selecting data to fit their hypothesis.

    I understand that Methods are often put at the end of a manuscript, but the measures discussed here are so fundamental to the analysis that a brief description of what the different measures are (in particular, the "alternative splicing ratio") should be in the main text, even when the mathematical definition can remain in the Methods.

    Finally, a few words on presentation. I understand that the following comments might read differently after the authors change their presentation. This manuscript was at the border of being comprehensible. In many cases, I could discern the meaning of words and sentences in contexts but sometimes even that failed (as an example above, about "species-specific trends", illustrates). The authors introduced jargon that does not have any meaning in the English language, and they do this over and over again.

    Note that I completely agree with all the comments by the other reviewer, who alerted me to problems I did not catch, including the possible correlation with effective population size: a possible non-adaptive explanation for the results.

  15. Arcadia Science

    Figure 3.

    Again, I'd strongly recommend reanalyzing these data (particularly 3B) using phylogenetic comparative methods! Although some taxonomic groups seem to exhibit a strong trend (e.g. flowing plants) others do not.

  16. Arcadia Science

    With some exceptions, alternative splicing is unrelated to genome factors (see Figure 2—figure Supplement 1, Figure 2—figure Supplement 2, and Figure 2—figure Supplement 3).

    This is where I would strongly suggest reanalyzing these data using phylogenetic comparative methods - you may be surprised to find that previously non-significant relationships become significant after using the more appropriate methods!

  17. Arcadia Science

    This percentage is much higher than in most multicellular life forms, where coding comprises less than 50% of genes.

    Are you referring to genes here? or the genome? In other words, do you mean to say that less than 50% of genes in most multicellular life forms are coding? Or do you perhaps mean to say that less than 50% of the genome is coding? If the latter (which is what I suspect you mean to say), I would revise throughout for clarity/accuracy.

  18. Arcadia Science

    Figure 1.

    This figure demonstrates clearly the strong effect of shared evolutonary history (i.e phylogeny) on the relationships recovered herein. Another potentially interesting analysis you could consider here is a phylogenetic analysis of covariance (phylANCOVA - originally published by Fuentes-G et al., 2016 - https://doi.org/10.1086/688917).

    This test is effectively equivalent to a normal ANCOVA in that it formally tests whether different groups (here, taxonomic groups) are best explained by different regression models. In other words whether groups share slopes, intercepts, or both. The difference is that the test can account for evolutionary non-independence using a phylogeny - this test could be conducted using the a phylogeny comprised of the full suite of species for which you have these data.

    This could be a nice way to formally assess which groups should actually be modeled separately, and assessing whether differences among groups are statistically significant. Currently, difference among groups is implicitly assumed, by modeling each using their own model.

  20. Arcadia Science

    Genome, genes, and coding sizes increase proportionally to each other at a lineage-specific level (see Figure 1—figure Supplement 1,Figure 1—figure Supplement 2, and Figure 1—figure Supplement 3). Specifically, we observe a significant correlation between each pair of genome variables in all cases, except for birds, where the genome size is weakly correlated to gene content and coding DNA. Furthermore, the slopes given by the linear regressions differ for each taxonomic group, which suggests key differences in their genome evolution. Figure 1A-C shows the relationship between each pair of genome variables, differentiated by each taxonomic group. Because genome variables are related to each other in an embedding structure, we show in Figure 1D the relation between the percentage of coding composing genes and the respective percentage of gene content in genomes.

    To conduct your regressions in a manner that is statistically robust to evolutionary non-independence within each taxonomic group, I suggest you conduct phylogenetic least squares (PGLS). This can be conducted in a very straightforward manner using R (for instance, as described here: http://www.phytools.org/Cordoba2017/ex/4/PGLS.html). All you will need is:

    1. The per-species measurements (i.e. genome size, gene content, length of coding sequence, etc), and
    2. a time-calibrated phylogeny (branch lengths are in units of time) that contains the species for which you have these data.

    Since you have measurements for so many species (a fantastic dataset!), I might suggest simply curating your list of species and obtaining a phylogeny from timetree.org. These phylogenies will not necessarily be the most accurate, as they are effectively aggregated from the published literature, but they should be sufficient for your purposes. Although these phylogenies my not include all species in your dataset, they may include closely related, representative species that you can use in their stead.

    Even if this approach requires the removal of some species in your data, use of phylogenetic comparative methods like PGLS are critical for the statistically robust analysis of these data, and thus interpretations reached herein. Without conducting these improved analyses, it unfortunately will be impossible to evaluate the accuracy of the results presented here, particularly with respect to parameter estimates, and differences in the role of alternative splicing in driving the evolution of genome complexity.

  21. Arcadia Science

    Thus, a comparative analysis of species spanning the whole tree of life has revealed certain evolutionary trends in alternative splicing, prevalence in specific lineages, and relation to genome compositional structures.

    I really do like the idea of the metric you've come up with here, but my major concern is that in these correlative tests you have not accounted for the confounding effect of evolutionary non-independence between species (Felsenstein 1985: https://www.jstor.org/stable/2461605).

    That is, because species share evolutionary histories, more closely related species will be more similar in their phenotypes and relevant to this study, in their genome content. This induces, in effect, statistical non-independence of species - phylogenetic pseudoreplication - that must be accounted for formally in your statistical analyses.

    Failure to do so can lead to (for instance), biased or incorrect parameter estimates (both intercept and slope) within models (i.e. within taxonomic group), and can confound or mislead interpretations among groups (i.e. among models fit for each taxonomic group). Fortunately, the solution is relatively straightforward - I've detailed some fixes in the sections below.

  22. Arcadia Science

    high taxonomic groups

    I would suggest avoiding language such as this, since it alludes the the inaccurate "Scala Naturae"-type ladderized view of evolution, progressing from "low" complexity organisms towards "higher" complexity multicellular organisms.

  23. Arcadia Science

    Transcript diversification is driven by two main mechanisms: gene duplication (Lynch and Conery, 2000; Holland et al., 2017) and alternative splicing (Bush et al., 2017)

    Maybe specify "of extant genes" to clarify how these two processes are not inclusive of the formation of ALL new transcripts, including those for genes not yet contained within the genome of a given lineage. That is, horizontal gene transfer and de novo gene birth are also two common mechanisms by which new genes (and thus transcript diversity) arises.

  24. Version published to 10.1101/2023.12.26.571677 on bioRxiv