No evidence for disassortative mating based on HLA in a small-scale, endogamous population

Reviewer #1 (Public review):

Summary:

This study aims to test whether human mate choice is influenced by HLA similarity while accounting for genome-wide relatedness, using the Himba as an evolutionarily relevant small-scale society population, unique among most HLA-mate choice studies. By comparing self-chosen ("love") and arranged marriages and using NGS-based 8-locus HLA class I and II sequences and genome-wide SNP data, the authors ask whether partners who freely choose each other are more HLA-dissimilar than those paired through social arrangements or random pairs. They further extend their work by examining functional differences in peptide-binding divergence among pairs and predicted pathogen recognition in potential offspring.

Strengths:

This study has many strengths. The most obvious is their ability to test for HLA-based mate choice in the Himba, a non-European, non-admixed, small-scale society population, the type of population that has been missing, in my opinion, from the majority of HLA mate choice studies. While Hedrick and Black (1997) used a similarly evolutionarily relevant remote tribe of native South Americans, they only considered 2 class I loci (HLA-A and HLA-B) at the first typing field (serological allele group) and did not have data for genome-wide relatedness. The Himba are also unique among previously studied populations because they have both socially arranged and self-chosen partnerships, so the authors could test if freely-chosen partners had lower MHC-similarity than assigned or randomly chosen partners.

Another key strength of the study was the relatively large sample size (HLA allele calls from 366 individuals, 102 unrelated) and 219 individuals with HLA data, whole genome SNP data, and involved in a partnership.

The study was also unique among HLA-mate choice studies for comparing peptide binding region protein divergence (calculated as the Grantham distance between amino acid sequences) among partner types and randomly generated pairs. This was also the first time I have seen a study use peptide binding prediction analysis of relevant human pathogens for potential offspring among partners to test if there would be a pathogen-relevant fitness benefit of partner selection.

Weaknesses:

My main concerns relate to the reliance on imputed HLA haplotypes and on IBD-based metrics in a region of the genome where both approaches are known to be problematic.

First, several key results depend on HLA haplotypes inferred through imputation rather than directly observed sequence data. The authors trained HIBAG imputation models on Himba SNP data across the full 5 Mb HLA region using paired HLA allele calls from target capture sequencing (L251-253). However, the underlying SNP data were generated by mapping reads to a 1000 Genomes Yoruba reference, meaning that both SNP discovery and subsequent imputation depend on the haplotypes represented in that reference panel. As a result, the imputation framework is likely biased toward common haplotypes shared between the Himba and Yoruba populations, while rare or Himba-specific HLA alleles are less likely to be imputed accurately or at all. This limitation has been noted previously for HLA imputation, particularly for novel or low-frequency variants and for populations that are poorly represented in reference panels. While the authors compare (first-field) imputed alleles to sequenced alleles to assess imputation accuracy, this validation step itself may be biased toward the same common haplotypes that are easiest to impute. This becomes especially problematic if IBD is inferred using imputed haplotypes, because haplotype sharing would then primarily reflect common, reference-supported haplotypes, while true population-specific variation would be effectively invisible. In this scenario, downstream estimates of IBD sharing may be inflated for common haplotypes and deflated for rare ones, potentially biasing conclusions about haplotype sharing, selection, and mate choice at the HLA region.

Second, the interpretation of excess identity-by-descent (IBD) sharing in the HLA region is difficult given the well-documented genomic properties of this locus. The classical HLA region is highly gene-dense, structurally complex, and characterized by extreme heterogeneity in recombination rates, with pronounced hot- and cold-spots (Miretti et al. 2005; de Bakker et al. 2006, reviewed in Radwan et al. 2020). Elevated IBD in such regions can arise from low recombination, background selection, or demographic processes such as bottlenecks, all of which can mimic signals of recent positive selection. While the authors suggest fluctuating or directional selection, extensive haplotype sharing is also consistent with long-term balancing selection at the MHC (Albrechtsen et al. 2010) or recent demographic history in this population.

Beyond these main issues, there are several additional concerns that affect interpretation. Sample sizes and partnership counts are sometimes unclear; some figures would benefit from clearer scaling (Figure 1) and annotation (Figures S6 and S7), and key methodological choices (e.g., treatment of DRB copy number variation, no recombination correction in IBD calling) require further explanation. Finally, some conclusions, particularly those invoking optimality or specific selective mechanisms, are not directly tested by the analyses presented and would benefit from more cautious framing.

Reviewer #2 (Public review):

Summary:

Evidence for the influence of MHC on mate choice in humans is challenging, as social structures and norms often confound the power of studying populations. This study uses an unusual, diverse, but relatively isolated population that allows a direct comparison of arranged and chosen partners to determine if MHC diversity is increased when choice drives mate choice. Overall, the authors use a range of genetic analyses to determine individual relationships alongside different measures of MHC diversity and potential selection pressures. The overall finding that there is no heterozygous dissimilarity difference between arranged and chosen partners. There is evidence of positive selection that may be a stronger driver, or at least it may mask other selection forces.

Strengths:

A rare opportunity to study human mate choice and genetic diversity. An excellent range of data and analysis that is well applied, and all results point to the same conclusion.

Overall, this is a very well-written and concise paper when considering the significant amount of data and excellent analysis that has been undertaken.

Weaknesses:

(1) For the type of samples and data available, none are obvious.

(2) Although this paper is clearly focused on humans, I was expecting more discussion around the studies that have been undertaken in animals. It is likely that between populations and species, there are different pressures that have driven the MHC evolution, but also mate choice.

(3) The peptide presentation based on pathogen genomes is interesting but usually not significant. I wondered if another measure of MHC haplotype diversity to complement this would be the overall repertoire of peptides that could be presented, pathogen-based or otherwise. There is usually significant overlap in the peptides that can be presented, for example, between HLA-A and HLA-B, and this may reveal more significant differences between the alleles and haplotype frequencies.

Reviewer #3 (Public review):

The study investigates MHC-related mate choice in humans using a sample of couples from a small-scale sub-Saharan society. This is an important endeavour, as the vast majority of previous studies have been based on samples from complex, highly structured societies that are unlikely to reflect most of human evolutionary history. Moreover, the study controls for genome-wide diversity, allowing for a test of the specificity of the MHC region, as theoretically predicted. Finally, the authors examine potential fitness benefits by analysing predicted pathogen-binding affinities. Across all analyses, no deviations from random pairing are detected, suggesting a limited role for MHC-related mate choice in a relatively homogeneous society. Overall, I find the study to be carefully executed, and the paper clearly written. Nevertheless, I believe the paper would benefit if the following points were considered:

(1) The authors claim (p. 2, l. 85) that their study is the first to employ a non-European small-scale society. I believe this claim is incorrect, as Hendrick and Black (1997) investigated MHC similarity among couples from South American indigenous populations.

(2) Regarding the argument that in complex societies, mating with a random individual would already result in sufficient MHC dissimilarity (p. 2, 78), see the paper from Croy et al. 2020, which used the largest sample to date in this research area.

(3) Dataset. As some relationships are parallel, I assume that certain individuals entered the dataset multiple times. This should be explicitly reported in the Methods. If I understand the analyses correctly, this non-independence was addressed by including individual identity as a random effect in the model - the authors should confirm whether this is the case. I am also wondering to what extent so-called "discovered partnerships" may affect the results. Shared offspring may be the outcome of short or transient affairs and could have a different social status compared with other informal relationships. Would the observed patterns change if these partnerships were excluded from the analyses?

(4) How many pairs were due to relatedness closer than 3rd degree? In addition, why was 4th degree relatedness used as a threshold in some of the other analyses?

(5) I was surprised by the exclusion of HIV, given that Namibia has a very high prevalence of HIV in the general population (e.g., Low et al. 2021).

(6) It appears that age criteria were applied when generating random pairs (p. 8, l. 350). Could the authors please specify what they consider a realistic age gap, and on what basis this threshold was chosen? As these are virtual couples used solely to estimate random variation within the population, it is not entirely clear why age constraints are necessary. Would the observed patterns change if no age criteria were applied?

(7) I think it would be helpful for readers if the Results section explicitly stated that real couples did not differ from randomly generated pairs. At present, only the comparison between chosen and arranged pairs is reported.

(8) I appreciate the separate analyses of pathogen-binding properties for MHC class I and class II, given their functional distinctiveness. For the same reason, I would welcome a parallel analysis of MHC sharing conducted separately for class I and class II loci.

(9) I think the Discussion would benefit from a more detailed comparison with previous studies. In addition, the manuscript does not explicitly address limitations of the current study, including the relatively limited sample size given the extensive polymorphism in the MHC region.

References:

Hedrick, P. W., & Black, F. L. (1997). HLA and mate selection: no evidence in South Amerindians. The American Journal of Human Genetics, 61(3), 505-511.

Croy, I., Ritschel, G., Kreßner-Kiel, D., Schäfer, L., Hummel, T., Havlíček, J., ... & Schmidt, A. H. (2020). Marriage does not relate to major histocompatibility complex: A genetic analysis based on 3691 couples. Proceedings of the Royal Society B, 287(1936), 20201800.

Low, A., Sachathep, K., Rutherford, G., Nitschke, A. M., Wolkon, A., Banda, K., ... & Mutenda, N. (2021). Migration in Namibia and its association with HIV acquisition and treatment outcomes. PLoS One, 16(9), e0256865.

Author Response

Reviewer 1 (Public review):

Summary:

This study aims to test whether human mate choice is influenced by HLA similarity while accounting for genome-wide relatedness, using the Himba as an evolutionarily relevant small-scale society population, unique among most HLA-mate choice studies. By comparing self-chosen ("love") and arranged marriages and using NGS-based 8-locus HLA class I and II sequences and genome-wide SNP data, the authors ask whether partners who freely choose each other are more HLA-dissimilar than those paired through social arrangements or random pairs. They further extend their work by examining functional differences in peptide-binding divergence among pairs and predicted pathogen recognition in potential offspring.

Strengths:

This study has many strengths. The most obvious is their ability to test for HLA-based mate choice in the Himba, a non-European, non-admixed, small-scale society population, the type of population that has been missing, in my opinion, from the majority of HLA mate choice studies. While Hedrick and Black (1997) used a similarly evolutionarily relevant remote tribe of native South Americans, they only considered 2 class I loci (HLA-A and HLA-B) at the first typing field (serological allele group) and did not have data for genome-wide relatedness. The Himba are also unique among previously studied populations because they have both socially arranged and self-chosen partnerships, so the authors could test if freely-chosen partners had lower MHC-similarity than assigned or randomly chosen partners.

Another key strength of the study was the relatively large sample size (HLA allele calls from 366 individuals, 102 unrelated) and 219 individuals with HLA data, whole genome SNP data, and involved in a partnership.

The study was also unique among HLA-mate choice studies for comparing peptide binding region protein divergence (calculated as the Grantham distance between amino acid sequences) among partner types and randomly generated pairs. This was also the first time I have seen a study use peptide binding prediction analysis of relevant human pathogens for potential offspring among partners to test if there would be a pathogen-relevant fitness benefit of partner selection.

Weaknesses:

My main concerns relate to the reliance on imputed HLA haplotypes and on IBD-based metrics in a region of the genome where both approaches are known to be problematic.

First, several key results depend on HLA haplotypes inferred through imputation rather than directly observed sequence data. The authors trained HIBAG imputation models on Himba SNP data across the full 5 Mb HLA region using paired HLA allele calls from target capture sequencing (L251-253). However, the underlying SNP data were generated by mapping reads to a 1000 Genomes Yoruba reference, meaning that both SNP discovery and subsequent imputation depend on the haplotypes represented in that reference panel. As a result, the imputation framework is likely biased toward common haplotypes shared between the Himba and Yoruba populations, while rare or Himba-specific HLA alleles are less likely to be imputed accurately or at all. This limitation has been noted previously for HLA imputation, particularly for novel or low-frequency variants and for populations that are poorly represented in reference panels. While the authors compare (first-field) imputed alleles to sequenced alleles to assess imputation accuracy, this validation step itself may be biased toward the same common haplotypes that are easiest to impute. This becomes especially problematic if IBD is inferred using imputed haplotypes, because haplotype sharing would then primarily reflect common, reference-supported haplotypes, while true population-specific variation would be effectively invisible. In this scenario, downstream estimates of IBD sharing may be inflated for common haplotypes and deflated for rare ones, potentially biasing conclusions about haplotype sharing, selection, and mate choice at the HLA region.

We appreciate the reviewer's concern, but would like to clarify two important misunderstandings in this assessment.

First, the reviewer suggests that our SNP data were generated by mapping reads to a 1000 Genomes Yoruba reference, and that IBD inference may therefore be biased toward haplotypes common between the Himba and Yoruba. This is not the case. Our SNP genotype data were generated from the H3Africa and MEGAex genotyping arrays, which incorporated diverse reference variation to minimize ascertainment bias in non-European ancestries. No read mapping to a Yoruba reference genome was involved in SNP discovery or genotyping. The Yoruba 1000 Genomes data were used solely to provide an ancestry-matched recombination map for phasing and IBD calling–this would not bias IBD inference toward common Yoruba haplotypes. The reviewer's concern about imputation-driven inflation of IBD sharing for common haplotypes should not be relevant in our case.

Second, regarding HLA haplotype resolution: we trained a bespoke HIBAG model directly on the Himba SNP array genotype data paired with ground-truth HLA allele calls from our own targeted HLA capture sequencing. This Himba-specific model was then used to impute HLA alleles from pseudo-homozygous genotypes derived by extracting phased SNP-based haplotypes across the HLA region for the same individuals. In this way we resolved the phase of the HLA allele calls.. To our knowledge, this paired-data approach to individual-level HLA haplotype resolution is novel; existing HLA haplotype resolution tools generally provide only population-level haplotype frequency estimates rather than individual-level phase assignments. We are confident in the reliability of the haplotypes we report. Resolved haplotypes were required to match the known targeted-sequencing HLA allele calls at a minimum of the first field for at least one allele, and both haplotypes could not be assigned to the same allele unless the individual's HLA allele calls were homozygous. Of 722 total haplotypes, 698 were successfully resolved under these criteria. We report results only on these confidently resolved haplotypes.

Second, the interpretation of excess identity-by-descent (IBD) sharing in the HLA region is difficult given the well-documented genomic properties of this locus. The classical HLA region is highly gene-dense, structurally complex, and characterized by extreme heterogeneity in recombination rates, with pronounced hot- and cold-spots (Miretti et al. 2005; de Bakker et al. 2006, reviewed in Radwan et al. 2020). Elevated IBD in such regions can arise from low recombination, background selection, or demographic processes such as bottlenecks, all of which can mimic signals of recent positive selection. While the authors suggest fluctuating or directional selection, extensive haplotype sharing is also consistent with long-term balancing selection at the MHC (Albrechtsen et al. 2010) or recent demographic history in this population.

We thank the reviewer for highlighting the difficulty in modeling selection at the HLA - a problem that deserves considerable attention. We acknowledge that demographic processes such as the documented Himba population bottleneck can result in elevated IBD sharing (Swinford et al. 2023, PNAS). However, our comparison of HLA IBD sharing rates against a genome-wide baseline is designed to address this: demographic processes affect all regions of the genome, so if the HLA region maintains elevated IBD sharing significantly above the genome-wide threshold, this provides meaningful evidence for a locus-specific effect beyond demographic history alone.

We agree with the reviewer that the recombination landscape of the HLA region is complex, but this complexity itself is consistent with the region being a frequent target of selection. Previous HLA analyses have found that at the allele level, frequencies are consistent with balancing selection, while multi-locus haplotype frequencies are consistent with purifying selection and positive frequency-dependent selection (Alter et al., 2017), patterns that contribute to the complex recombination rate heterogeneity observed in the region. Recombination rate can be both a cause of extended haplotypes but also the consequence of selection against combinations of alleles.

As Alter et al. note, the high levels of linkage disequilibrium observed among HLA alleles serve to limit the amount of diversity within HLA haplotypes, but balancing selection at the allelic level maintains multiple HLA haplotypes at high frequency across populations over long periods of time — so-called "conserved extended haplotypes" as we observe (Supplementary Figures 1 and 9). Regarding the specific selective mechanism, our results are not equally consistent with all forms of balancing selection. Albrechtsen et al. (2010) explicitly modeled overdominant balancing selection and demonstrated that equilibrium overdominance does not produce elevated IBD sharing as we observe — our results are therefore inconsistent with this mechanism. Instead, Albrechtsen et al. conclude that allele frequency change is required to generate elevated IBD, consistent with bouts of directional selection such as negative frequency-dependent or fluctuating positive selection. We will make explicit that while our findings do not support overdominance, they are consistent with these temporally dynamic forms of selection driving periodic allele frequency change at the HLA locus. We will also incorporate local recombination rate into Figure 4 to provide a comparison of local recombination rate across chromosome 6 with the observed areas of elevated IBD sharing.

Alter, I., Gragert, L., Fingerson, S., Maiers, M., & Louzoun, Y. (2017). HLA class I haplotype diversity is consistent with selection for frequent existing haplotypes. PLoS computational biology, 13(8), e1005693.

Beyond these main issues, there are several additional concerns that affect interpretation. Sample sizes and partnership counts are sometimes unclear; some figures would benefit from clearer scaling (Figure 1) and annotation (Figures S6 and S7), and key methodological choices (e.g., treatment of DRB copy number variation, no recombination correction in IBD calling) require further explanation. Finally, some conclusions, particularly those invoking optimality or specific selective mechanisms, are not directly tested by the analyses presented and would benefit from more cautious framing.

We will clarify the presentation of partnership counts and sample sizes throughout the manuscript and improve the scaling and annotation of the flagged figures. Regarding DRB copy number variation, we will add explicit discussion of our analytical choices and their potential limitations. As described in our responses to the main concerns above, we will also provide more nuanced framing of the selective mechanisms consistent with our IBD results, avoiding conclusions that go beyond what our analyses directly support.

Reviewer #2 (Public review):

Summary:

Evidence for the influence of MHC on mate choice in humans is challenging, as social structures and norms often confound the power of studying populations. This study uses an unusual, diverse, but relatively isolated population that allows a direct comparison of arranged and chosen partners to determine if MHC diversity is increased when choice drives mate choice. Overall, the authors use a range of genetic analyses to determine individual relationships alongside different measures of MHC diversity and potential selection pressures. The overall finding that there is no heterozygous dissimilarity difference between arranged and chosen partners. There is evidence of positive selection that may be a stronger driver, or at least it may mask other selection forces.

Strengths:

A rare opportunity to study human mate choice and genetic diversity. An excellent range of data and analysis that is well applied, and all results point to the same conclusion.

Overall, this is a very well-written and concise paper when considering the significant amount of data and excellent analysis that has been undertaken.

Weaknesses:

(1) For the type of samples and data available, none are obvious.

(2) Although this paper is clearly focused on humans, I was expecting more discussion around the studies that have been undertaken in animals. It is likely that between populations and species, there are different pressures that have driven the MHC evolution, but also mate choice.

We will improve the framing of our project within the broader non-human MHC mate choice literature in our discussion.

(3) The peptide presentation based on pathogen genomes is interesting but usually not significant. I wondered if another measure of MHC haplotype diversity to complement this would be the overall repertoire of peptides that could be presented, pathogen-based or otherwise. There is usually significant overlap in the peptides that can be presented, for example, between HLA-A and HLA-B, and this may reveal more significant differences between the alleles and haplotype frequencies.

We would like to clarify that we did assess the unique pathogen peptides bound across all HLA class I and class II genes by each population's common haplotypes (Figures S12–S13). We acknowledge the reviewer's point that non-pathogenic peptides are also important — for example, binding with self-produced proteins. However, binding with self-produced proteins is more relevant to autoimmune risk, and the selective pressures involved are outside the scope of our current work, which focuses on pathogen-induced fluctuating directional selection and heterozygote advantage. Furthermore, selection on non-pathogenic peptide binding repertoires likely operates in the opposite direction to pathogen repertoire; whereas broader pathogen peptide binding is advantageous, broader self-peptide binding risks excessive immune activation.

Reviewer #3 (Public review):

The study investigates MHC-related mate choice in humans using a sample of couples from a small-scale sub-Saharan society. This is an important endeavour, as the vast majority of previous studies have been based on samples from complex, highly structured societies that are unlikely to reflect most of human evolutionary history. Moreover, the study controls for genome-wide diversity, allowing for a test of the specificity of the MHC region, as theoretically predicted. Finally, the authors examine potential fitness benefits by analysing predicted pathogen-binding affinities. Across all analyses, no deviations from random pairing are detected, suggesting a limited role for MHC-related mate choice in a relatively homogeneous society. Overall, I find the study to be carefully executed, and the paper clearly written. Nevertheless, I believe the paper would benefit if the following points were considered:

(1) The authors claim (p. 2, l. 85) that their study is the first to employ a non-European small-scale society. I believe this claim is incorrect, as Hendrick and Black (1997) investigated MHC similarity among couples from South American indigenous populations.

We thank the reviewer for this important clarification. Our claim was intended to be more specific: to our knowledge, this is the first study to investigate HLA-based mate preferences in a non-European small-scale society while explicitly controlling for genome-wide relatedness. Hedrick and Black (1997) did not include genome-wide relatedness controls, which is a critical distinction given that ancestry-assortative mating can produce spurious patterns of HLA similarity or dissimilarity in the absence of such correction. We will make this qualification explicit in the revised manuscript.

(2) Regarding the argument that in complex societies, mating with a random individual would already result in sufficient MHC dissimilarity (p. 2, 78), see the paper from Croy et al. 2020, which used the largest sample to date in this research area.

We thank the reviewer for this reference. In our revision, we will incorporate Croy et al. (2020) into our discussion and use it as a reference for comparing the Himba’s probability of highly homozygous offspring given population allele frequencies. This comparison will help support our claim that background HLA diversity in the Himba is sufficiently high so that any unrelated partner is already likely to yield adequately dissimilar offspring—a scenario that would reduce the selective benefit of active HLA-based mate choice and could mask any such preference even if it exists.

(3) Dataset. As some relationships are parallel, I assume that certain individuals entered the dataset multiple times. This should be explicitly reported in the Methods. If I understand the analyses correctly, this non-independence was addressed by including individual identity as a random effect in the model - the authors should confirm whether this is the case. I am also wondering to what extent so-called "discovered partnerships" may affect the results. Shared offspring may be the outcome of short or transient affairs and could have a different social status compared with other informal relationships. Would the observed patterns change if these partnerships were excluded from the analyses?

The reviewer is correct that individuals appear multiple times in the dataset—some individuals are members of multiple known partnerships, and all individuals are additionally included many times across the full set of possible random heterosexual pairings that meet our age and relatedness criteria. This non-independence is explicitly addressed in our dyadic linear mixed models by including female ID and male ID as random effects, which account for each individual's unique contribution to their similarity scores across all pairings, both real and random. We explain this explicitly in the (n) Statistical Models section of the methods section.

Regarding discovered partnerships: we grouped these with reported informal partnerships in the current analyses due to modest sample sizes. We agree this is worth examining more carefully and will test, in our revision, whether treating discovered partnerships as a separate category, or excluding them entirely, meaningfully affects our results. We will report these analyses as a sensitivity check.

(4) How many pairs were due to relatedness closer than 3rd degree? In addition, why was 4th degree relatedness used as a threshold in some of the other analyses?

This information is reported in the (n) ‘Statistical Models section of the Methods’. No pairs were found to be closer than 3rd degree relatives. No arranged marriages were related at 3rd degree or closer; 1 love match marriage and 2 informal partnerships discovered through pedigree analysis were found to be 3rd degree relatives.

Regarding the difference in relatedness thresholds: we used a 4th degree cutoff to define the unrelated set of individuals for allele and haplotype frequency analyses (n=102), as even 3rd degree relatives would inflate allele frequency estimates. In contrast, we permitted 3rd degree relatives in the background distribution for the partnership analyses to reflect the stated cultural preference for cousin marriages in arranged unions—excluding them would have made the background distribution less representative of the actual mating pool. We explain both decisions in Methods sections (d) and (n).

(5) I was surprised by the exclusion of HIV, given that Namibia has a very high prevalence of HIV in the general population (e.g., Low et al. 2021).

While HIV prevalence is indeed high in Namibia generally, the Himba are a relatively isolated population and, based on personal communication with Dr. Ashley Hazel—who has extensive field experience studying sexually transmitted infections in the Himba (see references 36, 52, 53, and 54)—there is no evidence of HIV transmission within this population. Dr. Hazel's expertise on this question was the basis for our exclusion of HIV from the pathogen list.

(6) It appears that age criteria were applied when generating random pairs (p. 8, l. 350). Could the authors please specify what they consider a realistic age gap, and on what basis this threshold was chosen? As these are virtual couples used solely to estimate random variation within the population, it is not entirely clear why age constraints are necessary. Would the observed patterns change if no age criteria were applied?

We will clarify this in our revision, but we restricted random couples to have an age gap within the range observed in actual, known partnerships (the woman is maximum 16 years older than then man and minimum 53 years younger than the man). We included this criteria to make sure random couples represented the best approximation of background, realistic partners. Our age gap criteria was quite permissive due to the large range observed in our actual pairs and we do not imagine it significantly impacted our results.

(7) I think it would be helpful for readers if the Results section explicitly stated that real couples did not differ from randomly generated pairs. At present, only the comparison between chosen and arranged pairs is reported.

We would like to clarify that for each analysis we explicitly report both the effects of chosen and arranged partnerships relative to the background distribution intercept, and the pairwise contrast between chosen and arranged partnerships. The intercept of each model is derived from the full background distribution of random opposite-sex pairings meeting our age and relatedness criteria, providing a null expectation under random mating. A non-significant effect for both partnership types therefore indicates that neither arranged nor chosen partnerships differ from random mating with respect to the metric in question. We describe this explicitly in the Statistical Models section of the Methods, but we will ensure this interpretation is stated more prominently in the Results section of the revised manuscript to avoid any confusion.

(8) I appreciate the separate analyses of pathogen-binding properties for MHC class I and class II, given their functional distinctiveness. For the same reason, I would welcome a parallel analysis of MHC sharing conducted separately for class I and class II loci.

We can incorporate separate HLA similarity/log odds of homozygous offspring analyses for class 1 and class 2 in our revision.

(9) I think the Discussion would benefit from a more detailed comparison with previous studies. In addition, the manuscript does not explicitly address limitations of the current study, including the relatively limited sample size given the extensive polymorphism in the MHC region.

We will expand our discussion in the revision to provide a more detailed comparison with previous studies, including Croy et al. (2020), and will add an explicit limitations section incorporating suggestions from multiple reviewers on more careful framing of optimality and specific selective mechanisms. Regarding sample size, we acknowledge this as a genuine limitation given the extensive polymorphism of the MHC region. However, our unrelated sample size used for allelic diversity estimated is comparable to previous studies in African populations (Figure 1), and our dataset is uniquely comprehensive in combining HLA class I, class II, genome-wide SNP data, and partnership data within the same individuals—a combination that enables the genome-wide relatedness correction that distinguishes our study from much of the prior literature.

References

Hedrick, P. W., & Black, F. L. (1997). HLA and mate selection: no evidence in South Amerindians. The American Journal of Human Genetics, 61(3), 505-511.

Croy, I., Ritschel, G., Kreßner-Kiel, D., Schäfer, L., Hummel, T., Havlíček, J., ... & Schmidt, A. H. (2020). Marriage does not relate to major histocompatibility complex: A genetic analysis based on 3691 couples. Proceedings of the Royal Society B, 287(1936), 20201800.

Low, A., Sachathep, K., Rutherford, G., Nitschke, A. M., Wolkon, A., Banda, K., ... & Mutenda, N. (2021). Migration in Namibia and its association with HIV acquisition and treatment outcomes. PLoS One, 16(9), e0256865.