replying to H. Shattuck-Heidorn et al. Nature https://doi.org/10.1038/s41586-021-03644 (2021)
In the accompanying Comment, Shattuck-Heidorn et al.1 argue that in our study2 the inferences are not supported by the data and the study is not appropriately contextualized within the empirical literature on the primary role of social factors in infectious disease epidemics. Our study should be read in the context of the large body of studies on the biological sex differences of immune responses. Many studies have shown that human immune responses against infections differ between the sexes3, and this is also the case in COVID-194,5. Such evidence in human studies is supported by a large body of animal studies that are devoid of any confounding social, behavioural and demographic factors, demonstrating that there are sex differences in immune responses across species, from fruitflies to mice3. In a mouse model of SARS-CoV, female mice are protected owing to the influence of female sex hormones on the immune system6. A recent study using a mouse model of SARS-CoV-2 infection also demonstrated a significant survival advantage in female mice7; male mice produce larger inflammatory responses with significantly higher expression of gene signatures of crucial cytokines and chemokines compared with female mice7, which is in line with our findings2. The role of sex and gender in the causal pathway is complex along the time course of infection (exposure, symptomatic illness, moderate and severe disease), and it involves biological and contextual factors. However, the purpose of our study was to examine the role of biological sex in immune responses among hospitalized patients, for which there is evidence of significant gender-based differences8.
Nevertheless, we are mindful of the limitations of our study, such as the small sample sizes, and of its exploratory nature; however, we disagree with the conclusion1 that our study “presents largely null findings that support an assessment of male–female similarities in immune response to the SARS-CoV-2 virus”.
Shattuck-Heidorn et al. constructed table 11 from our extended data tables 3–62 by classifying the data according to whether it was significant (that is, P < 0.05). They argue that some of the data that are significant in the baseline analysis are no longer significant after adjusting for age and body mass index (BMI), and that the factors in which there were statistically significant differences in the baseline analysis and the longitudinal analysis are not the same, suggesting a lack of consistency. Furthermore, the authors argue that differences reported in our study are largely null and maybe even artefactual.
Our study was an exploratory, and not a hypothesis-driven analysis, with a small sample size to provide a basis for further investigations. Therefore, although we used significance testing in our own interpretations, it is wrong to interpret any results that are not statistically significant results as disproving a hypothesis1—that is, to suggest that a lack of statistical significance indicates that there is no effect. P values are a useful tool but, as has been thoroughly discussed in the biostatistical literature9, it is inappropriate to interpret them in isolation from effect sizes, sample size and study design. Arguments based solely on P values lead to the dismissal of important differences. For example, by evaluating the magnitude and direction of the unadjusted and adjusted differences, as well as the statistical significance, in IL-8 and IL-18 levels between male and female patients in cohort A, we identified an important difference, which has been confirmed by others as discussed below. In addition, Shattuck-Heidorn et al.1 argue that significant differences in numbers of activated CD8 T cells between stable and deteriorated males disappears after adjusting for age and BMI. This is exactly what is expected—we clearly showed that deteriorated males were older, and exhibited lower T cell activation, and that these factors were strongly correlated only in males.
The claim that the factors in which statistical significance is detected in the baseline and longitudinal analyses should be ‘consistent’1 is based on an assumption that the same immune factors should be found in different phases of COVID-19 infection. Baseline analysis of cohort A included only the first time point, only for patients with moderate disease. The longitudinal analysis of cohort B included samples from later disease phases, with varying severity, and takes into account the overall immunological changes throughout the course of the disease. The immune response is a dynamic process involving innate and adaptive immunity10, and cytokine levels may change by orders of magnitude over time11. Thus, these analyses are fundamentally asking different questions and would not be expected to identify the same factors.
We are confused by the authors’ claim that the differences in immune phenotypes are largely null on the basis of biological sex, while at the same time they state that “observed differences in immune markers may reflect gendered chronic conditions”. The biological sex differences are closely intertwined with differences due to social and demographic gender disparities, and they are not mutually exclusive. We agree that analyses of the impact of gender disparities on immune responses are very important. However, this was not the focus of our study. We explicitly focused on the biological sex differences in the COVID-19 immune responses among a defined set of patients, and did not make general claims about the biological bases of gender disparities.
In less than half a year since the publication of our study, a large body of literature is emerging to support our findings. A single-cell transcriptomic study of peripheral blood mononuclear cells from patients with COVID-19 has revealed a significantly higher abundance of non-classical monocytes (ncMono) in male patients compared with female patients12, as we reported in our baseline analysis2, which is being dismissed by Shattuck-Heidorn et al. in their table 11. The ncMono abundance in male patients was twofold to fourfold higher compared with female patients12—the same magnitude of difference as in our study2. In addition, IL18 expression in monocytes from male patients was significantly higher than in those from female patients12. Nasal squamous epithelial cells from male patients with COVID-19 also expressed higher levels of IL18 than those from female patients12. Male patients showed higher expression in monocytes of MYD88 and NFKB112, genes that encode direct regulators of pro-inflammatory cytokines including IL-8. The neutrophil:lymphocyte ratio was found to be higher in male patients13, and neutrophil activation was associated with IL-8 levels in patients with COVID-1914. Another study used single-cell RNA-sequencing analysis to demonstrate prominent sex differences in CD8 T cells and especially in the subpopulation of CD161hi mucosal-associated invariant T cells (MAIT cells)15. MAIT cells in males exhibited pro-apoptotic gene signatures, whereas the same cell type in females had a different set of activated gene signatures, and bioinformatic analysis of gene-expression patterns indicated that these cells interact with monocytes through CCL5–CCR1 and IL18–IL-18R ligand–receptor interactions15; IL-18 and CCL5 are the same factors for which we reported sex differences in our baseline and longitudinal analyses, respectively2. The striking concordance between our findings and others on sex differences that implicate the same parameters and associated immune pathways makes it highly unlikely that our findings are artefactual. Independent studies including ours, using different modalities and methods, support sex differences in the same immune factors and pathways.
Finally, referring to our study2, Shattuck-Heidorn et al. state1 that “We stress that in no way does this study provide a foundation for clinical practice or for public health strategies to ameliorate COVID-19 sex disparities”. We simply stated that our analyses “provide a potential basis for taking sex-dependent approaches to prognosis, prevention, care, and therapy for patient with COVID-19”. Science is an iterative process. Although our study in isolation may only contribute a piece of the puzzle, given the large body of studies that demonstrate sex differences during the course of COVID-19 disease and the immune response as outlined above, it is perhaps time to take these collective insights into account for future guidance in developing clinical practice and public health strategies to improve treatment and prevention for COVID-19.
In conclusion, accumulating evidence supports an important role for biological sex in immune responses against COVID-19. The heterogeneity in the disease phenotype in COVID-19 is related to the intersectional nature of a variety of factors—social, gender, race, ethnicity, disability and economic, as well as geography, age and comorbidities16. We believe that biological sex should be included as a key variable for studying infectious diseases. We hope that more studies in this area will contribute to the better understanding of disease mechanisms, as well as to the development of better treatments against acute and long COVID-19.
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The authors declare no competing interests.
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Takahashi, T., Ellingson, M.K., Wong, P. et al. Reply to: A finding of sex similarities rather than differences in COVID-19 outcomes. Nature 597, E10–E11 (2021). https://doi.org/10.1038/s41586-021-03645-6