Submit to this Journal Review for this Journal Propose a Special Issue

Article Menu

Share Help Cite Discuss in SciProfiles

Open AccessArticle

Peer-Review Record

Genome-Wide and Locus-Level Analyses Reveal Modest, Heterogeneous Genetic Sharing Between Alzheimer’s Disease and Myasthenia Gravis

Int. J. Mol. Sci. 2026, 27(11), 4792; https://doi.org/10.3390/ijms27114792

by Emmanuel O. Adewuyi^1,2,3,4,*

, Asa Auta⁵, Chinedu I. Ossai⁶

, Chidozie C. Anyaegbu^2,7

, Thi Thu Huong Nguyen¹

, Md Rezanur Rahman⁸

, Blossom C. M. Stephan⁴

, Gizachew A. Tessema^1,2,9

, Dale R. Nyholt¹⁰

and Gavin Pereira^1,9,11

Reviewer 1:

Valentino Rački

Reviewer 2: Anonymous

Reviewer 3: Anonymous

Reviewer 4: Anonymous

Reviewer 5: Anonymous

Int. J. Mol. Sci. 2026, 27(11), 4792; https://doi.org/10.3390/ijms27114792

Submission received: 11 April 2026 / Revised: 15 May 2026 / Accepted: 22 May 2026 / Published: 26 May 2026

(This article belongs to the Special Issue Genomics of Human Disease)

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

This manuscript investigates the genetic relationship between Alzheimer’s disease and myasthenia gravis using a comprehensive multi-layered analytical framework, including genome-wide correlation, local genetic analyses, cross-trait meta-analysis, Mendelian randomisation, and gene-level approaches. The topic is original and clinically relevant, particularly given the growing interest in immune mechanisms in neurodegeneration and potential cross-disease biology. The study is methodologically ambitious and integrates multiple complementary approaches, which represents a clear strength. The manuscript is generally well written and logically structured. However, several important methodological, interpretational, and conceptual issues limit the strength of the conclusions and should be addressed to improve the robustness and clarity of the work.

Q1. Interpretation of modest genome-wide signal versus strong narrative conclusions
The genome-wide genetic correlation between Alzheimer’s disease and myasthenia gravis is nominal and does not survive correction for multiple testing. Despite this, the manuscript places considerable emphasis on shared genetic architecture. While the local and gene-level findings are interesting, the overall narrative may overstate the degree of shared genetic basis. The discussion should be more balanced and clearly distinguish between weak global overlap and more localized signals, avoiding any implication of a strong genome-wide relationship.

Q2. Heavy reliance on MHC region and potential confounding
A substantial proportion of the shared signals, including gene-level overlap and local correlations, are concentrated within the MHC region. Given the complex linkage disequilibrium structure and pleiotropic nature of this region, there is a risk that these findings reflect general immune-related architecture rather than disease-specific overlap. The manuscript would benefit from a more cautious interpretation of MHC-driven results and additional analyses demonstrating whether signals persist outside this region or after stricter conditioning.

Q3. Heterogeneity across MG subtypes
The results indicate substantial heterogeneity between early-onset and late-onset myasthenia gravis, with inconsistent or weak associations with Alzheimer’s disease across subtypes. However, this heterogeneity is not sufficiently integrated into the overall interpretation. The manuscript would be strengthened by a clearer discussion of subtype-specific mechanisms and by avoiding generalized conclusions about MG as a single entity.

Q4. Mendelian randomisation and causal inference
The Mendelian randomisation analysis suggests at most a weak and inconsistent causal effect of MG on AD, with no evidence for reverse causality. However, the number of instrumental variables is limited and replication analyses do not confirm the findings. The current interpretation appears somewhat stronger than warranted. The authors should more clearly emphasise the exploratory nature of these results and explicitly acknowledge the limited statistical power and potential for bias.

Q5. Cross-trait meta-analysis and novelty claims
The cross-trait GWAS meta-analysis identifies several loci reaching genome-wide significance after meta-analysis, including regions within chromosome 6 and 16. However, many of these signals are driven by known AD loci or immune-related regions. The manuscript would benefit from a more cautious interpretation of novelty, clearly distinguishing between truly novel shared loci and known disease-associated regions showing secondary signals.

Q6. Colocalisation analysis and interpretation
The colocalisation results predominantly support distinct causal variants within shared loci rather than true pleiotropic variants. This is an important finding, but its implications are not fully explored. The discussion should more clearly emphasise that shared regions do not necessarily imply shared causal mechanisms and should integrate this with the overall conclusion regarding heterogeneous genetic architecture.

Q7. Gene-level overlap and pathway interpretation
The gene-level analyses show statistically significant overlap, particularly at less stringent thresholds. However, the biological interpretation of these findings may be overly broad, especially given that many genes are located within immune-related regions. The manuscript would benefit from a more critical discussion of whether these findings reflect true disease-specific biology or general immune system involvement.

Q8. Multiple testing and statistical thresholds
While multiple testing correction is applied in some analyses, it is not always consistently emphasised across all sections. In particular, nominally significant findings are sometimes discussed alongside corrected results without clear distinction. The manuscript would benefit from a more consistent and transparent reporting of significance thresholds and a clearer separation between exploratory and robust findings.

Q9. Clinical and biological interpretation
The manuscript proposes a shared immune-centred regulatory architecture linking the two disorders. While this is plausible, the current evidence supports a more nuanced interpretation involving modest overlap and substantial heterogeneity. The clinical implications, particularly regarding shared pathophysiology or therapeutic targeting, should be discussed more cautiously and aligned with the strength of the evidence.

Q10. Clarity and presentation
The manuscript is generally well structured, but some sections, particularly the Results, are dense and highly technical. The inclusion of clearer summaries or schematic interpretations of key findings would improve readability. Figures are informative, but their interpretation could be more explicitly guided in the text. Minor language editing would further improve clarity and flow.

Author Response

Comment: This manuscript investigates the genetic relationship between Alzheimer’s disease and myasthenia gravis using a comprehensive multi-layered analytical framework, including genome-wide correlation, local genetic analyses, cross-trait meta-analysis, Mendelian randomisation, and gene-level approaches. The topic is original and clinically relevant, particularly given the growing interest in immune mechanisms in neurodegeneration and potential cross-disease biology. The study is methodologically ambitious and integrates multiple complementary approaches, which represents a clear strength. The manuscript is generally well written and logically structured. However, several important methodological, interpretational, and conceptual issues limit the strength of the conclusions and should be addressed to improve the robustness and clarity of the work.

Response: We thank the reviewer for the thoughtful assessment and recognition of the study’s novelty and clinical relevance. We have carefully revised the manuscript to address the raised methodological and interpretational concerns, improving clarity, strengthening the analytical description, and refining the discussion to better reflect the limits of the evidence. We believe these changes have further improved the manuscript.

Response: We agree that the genome-wide genetic correlation between AD and MG is modest and does not survive correction for multiple testing. However, weak global correlation does not preclude meaningful shared genetic architecture where effects are localised and heterogeneous across loci, which can attenuate genome-wide estimates. Accordingly, our interpretation is based on convergent evidence across complementary analyses, including local genetic correlation, cross-trait meta-analysis, colocalisation, and gene-level overlap, which together support modest, locus-specific sharing rather than broad genome-wide alignment. To better reflect this distinction, we revised the manuscript throughout to avoid overstating diffuse polygenic sharing.

Abstract: We replaced ‘sharing’ with ‘overlap’ when referring to genome-wide results and revised the conclusion to emphasise ‘modest global polygenic overlap’ and ‘pronounced locus-specific heterogeneity’.

Results: We retained the genome-wide correlation as nominal evidence and revised the SECA interpretation from ‘genome-wide polygenic alignment’ to ‘modest SNP-level concordance’.

Discussion: We softened statements implying diffuse genome-wide sharing and clarified that heterogeneous regional effects may attenuate global correlation estimates.

Conclusion: We revised this section and clearly distinguish modest, nominal genome‑wide overlap from stronger locus‑ and gene‑level findings, and consistently emphasise heterogeneity.

Response: We thank the reviewer for this important comment and agree that findings within the MHC region require cautious interpretation. However, the observed AD–MG overlap was not confined to the MHC region. Genome-wide correlation estimates remained stable (nominally) after excluding the MHC region, indicating that shared signals were not driven solely by the canonical immune locus. In addition, local genetic correlation identified non-MHC loci, and gene/SMR analyses prioritised putatively shared genes across multiple chromosomes, including 1, 16, 17, and 19. Importantly, local correlation analyses were not interpreted as evidence of shared causal variants within the MHC, but rather as evidence of regionally concentrated and heterogeneous genetic architecture. To further characterise these signals, we applied complementary analyses including heterogeneity-aware cross-trait meta-analysis and GWAS-PW colocalisation. Notably, most MHC regions showed patterns more consistent with distinct causal variants, whereas chromosome 16 provided clear evidence of potential non-MHC shared architecture across methods.

Moreover, the presence of heterogeneous and, in some cases, opposing local genetic correlations within the MHC regions argues against a simple explanation based on a uniform, non-specific immune background and instead supports a more complex, locus-specific architecture. We note that the manuscript consistently interpreted the AD–MG relationship cautiously, describing the overlap as modest, heterogeneous, and largely locus-specific, while noting that the genome-wide correlations did not survive multiple-testing correction. We have further clarified this interpretation in the revised manuscript to avoid overstating disease-specific overlap within the MHC region. Also, we noted limitation related to the MHC interpretation as follows: Fourth, the MHC region contains complex LD with multiple causal variants, and single signal colocalisation models may oversimplify this architecture; thus, MHC interpretations should be treated with caution pending conditional fine mapping (lines 916 – 919).

Response: We have revised the discussion to emphasise subtype-specific patterns. Specifically, we clarify that the absence of significant genome-wide correlations for MG subtypes likely reflects increased heterogeneity and reduced statistical power rather than the absence of shared genetic influences. We further highlight that locus-level analyses demonstrated stronger and more widespread associations for AD–LOMG than for AD–EOMG, with LOMG signals spanning both MHC and non-MHC loci, whereas AD–EOMG overlap was weaker and largely MHC restricted. These findings are consistent with known biological differences among MG subtypes and reinforce the view that the aggregate AD–MG signal reflects modest polygenic overlap, shaped by substantial subtype-specific heterogeneity, rather than a genetically uniform MG architecture. In addition, we now reflect this level of detail in the abstract and conclusion sections.

Response: We agree that the Mendelian randomisation (MR) findings should be interpreted cautiously. As reflected in the manuscript, we have framed these results as weak and exploratory and acknowledged several limitations relevant to causal inference. In the Results section, we described the MG→AD association as ‘weak’, ‘suggestive’, and ‘not convincing’, noting that it was based on a limited number of MG instruments (fewer than 10 IVs in the primary analysis) and was not supported by the replication dataset. In the discussion and limitations sections, we emphasised that the MR findings ‘warrant cautious interpretation’, and that the suggestive MG→AD effect did not replicate in a smaller AD GWAS, likely reflecting reduced power. In response to the reviewer’s comment, we have further clarified this framing by emphasising the exploratory nature of the MR analyses and tempering any language that could be perceived as implying robust causal inference.

Response: We clarify the interpretation of the cross‑trait GWAS meta‑analysis here. First, we did not claim broad novelty of genome‑wide significant loci. Novelty was discussed only in a clearly defined, trait‑contextual sense, specifically where variants were previously associated with one disorder (e.g., AD) but showed evidence of association with the other (e.g., putatively novel for MG), as exemplified by the chromosome 16 locus rs889555. Second, it is not the case that many signals identified after meta‑analysis are driven predominantly by known AD loci. Our analytical framework was designed to minimise this possibility. The meta‑analysis was heterogeneity‑aware and incorporated binary‑effect (BE) p‑values and m‑values to assess whether associations were supported in one or both traits and to differentiate signals driven primarily by a single trait. This is an important strength of our meta-analysis. Independent SNPs reaching genome-wide significance were largely supported by these metrics as reflecting cross-trait involvement. Third, meta‑analysis results were organised into categories distinguishing loci emerging only after meta‑analysis, known AD loci showing secondary evidence in MG, and loci primarily associated with MG, including immune‑related regions. Signals at established AD or immune loci were consistently interpreted as secondary or reinforcing cross‑trait evidence rather than as novel disease associations. We have further clarified this framing in the revised manuscript to avoid any ambiguity.

Response: As reported in the manuscript, colocalisation analyses predominantly supported distinct causal variants within shared loci (PPA4) rather than widespread variant‑level pleiotropy, suggesting that regional overlap does not necessarily imply shared causal mechanisms. We note this distinction in the discussion section and emphasise that most shared regions harbour distinct but closely linked causal variants. We also highlighted chromosome 16 as a notable exception, showing evidence consistent with a shared causal variant (PPA3). In response to the reviewer’s comment, we have further strengthened the discussion to more clearly integrate these findings into the overall conclusion, emphasising that AD–MG overlap primarily reflects region-level convergence with heterogeneous, locus-specific causal mechanisms rather than broad concordant sharing. For instance, we added:

‘Importantly, the predominance of PPA4 signals in our analysis suggests that shared genomic regions between AD and MG generally reflect distinct causal variants operating within the same loci [1]. The finding underscores that regional overlap does not imply shared causal mechanisms and is consistent with a heterogeneous, locus‑specific architecture.’(lines 813 – 817)

Response: We thank the reviewer for this comment. We want to clarify that the gene-level overlap analysis was specifically designed to quantify shared genetic contribution while mitigating LD-induced non-independence using the GEC framework, thereby reducing inflation from correlated genes, including those in the MHC. Consequently, the observed overlap is unlikely to be primarily driven by clustering of immune-related genes but instead reflects enrichment of approximately independent gene-level signals across the two traits. We agree that many downstream gene and pathway annotations involve immune-related biology, and that interpretation at this level should be cautious. However, our aim was not to infer disease-specific biology at the gene-overlap stage, but rather to characterise the extent of shared genetic architecture between AD and MG. Accordingly, we interpret the gene-level findings as evidence of shared association burden, while noting that such overlap does not imply shared causal variants or uniform biological mechanisms. More disease-relevant interpretation is therefore derived from complementary locus-level and regulatory analyses, which provide more specific insight into potential shared mechanisms and are discussed with appropriate caution. We have further clarified this distinction in the revised manuscript.

Response: In response to this comment, we have revised the manuscript to improve clarity and consistency in reporting. Specifically:

We now explicitly state the significance thresholds within each analytical section (e.g., Bonferroni correction in genome-wide and local correlation. etc.
We reflect the distinction between nominal and corrected findings in the Results and Discussion, and even in the abstract and conclusion sections.
We have refined wordings to separate primary (corrected) findings from supportive, nominal evidence.

We note that we do not reclassify nominal findings as purely exploratory, as this would not accurately reflect their intended methodological role. We believe these revisions enhance transparency while preserving the appropriate interpretive context of the results.

Response: We thank the reviewer for this important comment and agree that the interpretation should reflect modest overlap and substantial heterogeneity. In response, we have revised the manuscript to distinguish diffuse polygenic overlap from stronger locus-specific signals and to avoid any implication of uniform shared pathophysiology. Specifically, we have refined the Abstract, Discussion, and Conclusions to emphasise that AD–MG overlap is limited at the genome‑wide level, heterogeneous across loci (including within the MHC), and characterised by a mixture of concordant and discordant effects. We now describe the shared architecture more cautiously as partial and context‑dependent convergence, rather than a unified immune‑centred mechanism. In addition, clinical and therapeutic implications have been further moderated and consistently framed not as indicative of direct translational relevance. We believe these revisions align the interpretation closely with the strength and nature of the evidence.

Response: We recognise that some sections of the results are necessarily technical, given the multi-layered analytical framework employed. To improve readability, we have revised the text to include clearer summary statements that synthesise key findings and made our discussion clearer. We have also strengthened the accompanying narrative in the text to guide interpretation of the figures where appropriate. Finally, we have undertaken minor language editing throughout the manuscript to improve clarity and flow. We believe these changes enhance accessibility for a broader readership while preserving the technical detail required for transparency and reproducibility.

Reviewer 2 Report

Comments and Suggestions for Authors

The analytical framework is comprehensive and technically competent, employing state-of-the-art methods across multiple genomic resolutions. However, I have significant concerns about the specificity of the findings, the interpretive framing, the reliance on the MHC region, and several methodological and reporting issues that should be addressed before publication. Below I detail these concerns.

Major Concerns

Point 1 – The central limitation of this study is the absence of any demonstration that the AD–MG overlap is specific to MG rather than reflecting a generic AD–autoimmunity axis. A nominally significant rg ≈ 0.11, MHC-concentrated local correlations, HLA class II gene enrichment, and immune pathway hits would be expected for virtually any autoimmune disease paired with AD. Indeed, previous studies by the lead author and others have reported similar MHC-driven modest overlaps between AD and gastrointestinal disorders (Adewuyi et al., 2022, Communications Biology), and between AD and type 2 diabetes (Adewuyi et al., 2024, Communications Biology). Without a negative control analysis pairing AD with a phenotypically unrelated autoimmune condition (e.g., psoriasis, celiac disease, or rheumatoid arthritis) to demonstrate that the MG-specific overlap exceeds this background, the study cannot claim a “specific” relationship. The Discussion states the findings “define the AD–MG relationship” (line 54), but the current evidence is equally consistent with a nonspecific AD–immune axis. I recommend including at least one autoimmune negative control comparison, or substantially revising the interpretive framing to acknowledge this limitation explicitly.

Point 2 – The vast majority of shared loci, local genetic correlations, genome-wide significant shared genes (Table 5: all 8 sentinel genes are MHC class II), and pathway enrichments (antigen presentation, T-cell signalling) derive from the MHC region. Yet the Discussion emphasises that the genome-wide correlation “persisted after the exclusion of the APOE and MHC regions” (line 588) and that “genetic correlation is not driven solely by canonical loci” (line 590), implying robustness beyond MHC. This creates a contradictory narrative: during the Results section, the MHC is the central point of nearly every analysis (local correlations, gene-based overlap, SMR, pathways), while the Discussion downplays its dominance. If MHC is excluded, what remains? The chromosome 16 locus and a handful of suggestive signals. The authors should provide a systematic accounting: what fraction of the total shared signal (in terms of local rg, shared genes, enriched pathways) survives MHC exclusion? Without this, the non-MHC contribution cannot be evaluated.

Point 3 – The primary AD GWAS combines clinically diagnosed AD with AD-by-proxy cases (parental history from UK Biobank). This design increases sample size but dilutes genetic specificity (reported genetic correlation between clinical AD and proxy: rg ≈ 0.81, i.e. ∼19 % variance mismatch). Critically, when the clinically diagnosed AD dataset (Lambert et al., 2013) was used for SECA, no significant SNP-effect concordance with MG was observed (Ppermuted = 0.164 and 0.076; Section 2.3). This is a substantial discrepancy that receives insufficient attention. The SECA failure with clinical AD could mean: (a) the shared signal is partly driven by the proxy phenotype (which captures not only AD genetics but also survival bias and family structure effects), or (b) the Lambert GWAS is simply underpowered. The authors favour interpretation (b) but do not formally test it (e.g., via power analysis or simulation). The term “AD-by-proxy” should be explicitly defined in the Introduction or Methods, and the implications for signal specificity should be discussed more frankly.

Point 4 – The MR analysis of MG→AD uses fewer than 10 instruments, which is below the threshold for reliable MR inference (Burgess et al., 2011, Int J Epidemiol). The estimated OR of 1.013 is marginal and clinically negligible. The result did not replicate in the Lambert AD GWAS (IVW OR = 1.04, P = 0.37). The exploratory analysis at the suggestive threshold (P < 1 × 10⁻⁶) yielded a borderline P = 0.049 in only one model. Taken together, the evidence does not support even a “modest” causal effect; the appropriate summary is “inconclusive,” which the section title states (2.7) but the abstract and conclusion overstate. Additionally, winner’s curse may inflate MR estimates when GWS variants from an underpowered MG GWAS (∼5,700 cases) are used as instruments. Furthermore, horizontal pleiotropy assessment methodology (MR-Egger intercept, MR-PRESSO, HEIDI outlier detection) should be described in the main Methods section, not relegated entirely to the Supplementary Note.

Point 5 – Both AD and LOMG disproportionately affect individuals over 60 years of age. Age-related immune senescence, chronic low-grade inflammation (“inflamaging”), and general immune dysregulation are well-documented in this demographic. The tissue enrichment (Section 2.4) showing immune-cell heritability for both disorders, and the pathway enrichments (MHC class II antigen presentation, T-cell activation, interferon signalling) are entirely consistent with a shared age-related immune background rather than a disease-specific molecular link. The authors should discuss this alternative interpretation and, ideally, test whether the shared signal persists after conditioning on age-related immune activation loci or comparing against a non-immune-mediated age-related disease.

Point 6 – The Introduction cites epidemiological associations between MG and AD (OR ≈ 1.5) and cognitive impairment in MG patients. However, similar or stronger associations have been reported between AD and multiple sclerosis, rheumatoid arthritis, systemic lupus erythematosus, and type 1 diabetes (Yeung et al., 2022, J Psychiatr Res; Wotton & Goldacre, 2017). The meta-analysis of cognitive dysfunction in MG (Mao et al., 2015) reports deficits similar to those seen in other chronic autoimmune and inflammatory conditions. Without contextualising MG among other autoimmune diseases, the rationale for specifically studying AD–MG overlap rather than AD–autoimmunity broadly is not convincing. The Introduction should address: what makes MG uniquely relevant to AD beyond the shared cholinergic/immune features that are common to many autoimmune conditions?

Point 7 – No sex-stratified analysis despite known sex differences in both disorders. AD has a well-documented female preponderance (∼65% of cases), and MG exhibits a bimodal age-of-onset pattern with sex-dependent distribution (female predominance in EOMG, male in LOMG). Sex-specific GWAS for AD exist (e.g., Jansen et al. provide sex-stratified results), and ignoring sex may mask or inflate sex-specific genetic overlap. A sex-stratified analysis, or at minimum a discussion of why it was not performed, is warranted.

Specific Analytical and Reporting Concerns

Point 8 – The Introduction (line 62) begins with the same sentence as the Abstract (line 34): “Alzheimer’s disease (AD) and myasthenia gravis (MG) are clinically distinct disorders.” This should be rewritten to avoid redundancy.

Point 9 – Lines 81–82 state: “In AD, cholinergic dysfunction arises from the loss of basal forebrain neurons.” This presents a unidirectional causal chain (loss → dysfunction), but the relationship is more complex: cholinergic dysfunction may precede or contribute to neuronal loss, and non-neuronal cholinergic mechanisms are also implicated. The authors should soften this to “is associated with” rather than “arises from.”

Point 10 – Lines 90–91 discuss immune dysregulation in AD (microglial activation, pro-inflammatory pathways) but omit the emerging evidence for gut microbiome-mediated neuroinflammation via bacterial metabolites crossing the blood-brain barrier. Given that both AD and MG involve systemic immune dysregulation, and given the lead author’s prior work on AD–gastrointestinal overlap, this context is particularly relevant and should be mentioned.

Point 11 – The cited epidemiological association (4.28% AD in MG patients over 60 vs. 2.82% in general population; OR ≈ 1.5) may be confounded by healthcare utilisation bias: MG patients are under closer medical surveillance and more likely to receive dementia screening. Additionally, the comparison group (“general older population”) may include undiagnosed dementia. Were other dementias (vascular, Lewy body, frontotemporal) also elevated in MG patients? If so, the association is not AD-specific but reflects general neurodegenerative vulnerability.

Point 12 – The meta-analysis of cognitive impairment in MG (ref [2]) is presented as supporting the AD–MG biological link. However, cognitive dysfunction has been reported in numerous chronic autoimmune conditions (rheumatoid arthritis, SLE, multiple sclerosis, inflammatory bowel disease), likely reflecting systemic inflammation, fatigue, medication effects, and psychological burden. Would a random autoimmune disease show similar cognitive impairment profiles? This context is needed to evaluate the specificity of the AD–MG connection.

Point 13 – Page numbering resets after Table 5.

Point 14 – The authors transparently report that none of the AD–MG correlations survived Bonferroni correction (Section 2.2), yet the abstract and conclusions present the “modest polygenic overlap” without this qualification. All rg estimates are small (0.09–0.12), and the p-values (0.02–0.04) are only nominally significant. This should be more prominently acknowledged in the abstract.

Point 15 – The tissue-enrichment panel (Figure 2c) plots –log10(P) but does not indicate the significance threshold used. A horizontal line at P = 0.05 (or the FDR-corrected threshold, if applied) should be added for interpretability.

Point 16 – Tables 1–3 lack functional annotation columns. For a study emphasising biological interpretation, adding annotation columns would help readers assess the functional relevance of each locus without cross-referencing external databases.

Point 17 – In the AD–MG pairwise analysis (Table 2), locus 965 (chr6:32586785–32629239) shows rho = 0.19 with a confidence interval of 0.07–0.31. While statistically significant (P = 1.58 × 10⁻³), this is a notably small local correlation for a locus described as one of the key shared signals. In the AD–EOMG analysis, the same locus has rho = 0.10 (CI: 0.03–0.17), which is barely distinguishable from zero in practical terms. The text should acknowledge the modest magnitude of these effects.

Point 18 – The pairwise LAVA analysis reveals both positive and negative local correlations (e.g., chr18 in AD–MG, chr6 loci in AD–EOMG). The Discussion mentions these as “antagonistic pleiotropy” but does not formally test whether the mixture of concordant and discordant effects is statistically different from chance. Without such testing, the presence of opposing correlations could simply reflect noise in weakly powered local analyses. A permutation-based test of directionality heterogeneity would strengthen this interpretation.

Point 19 – In the second meta-analysis category (Section 2.6, line 334), SNPs that are GWS in AD and show “at least nominal significance in MG” are identified. The threshold for “nominal significance” (presumably P < 0.05) should be explicitly stated and justified. At P < 0.05, approximately 5% of all tested SNPs would be expected to show nominal association by chance; this is a weak evidentiary bar for claiming cross-trait involvement.

Point 20 – The colocalisation loci (Section 2.8) span up to ∼2.3 Mb (e.g., chr6:31.57–32.68 Mb), which is exceptionally large for fine-mapping. GWAS-PW assumes a relatively simple causal architecture within each region; in regions this size, especially the MHC, multiple independent signals likely exist, potentially confounding PPA3 vs PPA4 assignments. Additionally, chr16:29,036,613–31,379,355 is noted as “hg19” — why is this the only locus with an explicit build annotation? All coordinates throughout the paper should consistently specify the genome build (hg19 or hg38).

Point 21 – Table 4: effective independent gene count for overlap exceeds that for MG. At Pgene ≤ 0.1, the effective number of independent genes for the overlap set (577) appears disproportionately large relative to the raw overlap (980 genes, 704 observed in GEC, yielding 577 effective). While the GEC method accounts for LD differently across different gene sets, the authors should explain why the effective-to-observed ratio for the overlap (577/704 = 0.82) is higher than for either individual trait (0.80 for AD, 0.79 for MG). This may be a property of the method, but it is counterintuitive and should be clarified.

Point 22 – Several genes reported as MG-GWS showing AD association (Supplementary Table 9), such as NOTCH4 and C6orf15, are physically located within the extended MHC region but are not MHC-specific in function. NOTCH4 is involved in general developmental and vascular signalling; C6orf15 encodes a small secreted protein. Their inclusion in the “MHC-clustered” gene set without functional disambiguation could mislead readers into interpreting the entire MHC signal as immune-driven, when parts of it may reflect linkage disequilibrium with non-immune variants.

Point 23 – In Figure 3b, both bubble size and colour encode the same variable (–log10 pSMR). This is visually redundant and wastes a visual channel that could encode additional information (e.g., HEIDI p-value, effect direction, or tissue category). Consider using colour for one variable and size for another, or simplify to a heatmap.

Point 24 – The tissue-specific heritability enrichment (Section 2.4) and pathway analyses depend on curated gene sets from databases that are inherently biased toward well-studied tissues and cell types. Immune cells, blood, and brain are among the most extensively annotated; less-studied tissues (e.g., thymus, bone marrow niches) may be underrepresented. If the enrichment simply reflects annotation density rather than biological signal, the results could be misleading. The authors should discuss this potential ascertainment bias.

Point 25 – The genes identified outside the MHC (chr16: ZNF668, CFAP119, PRSS53, VKORC1; chr19: POLR2E, ABCA7, CNN2, GPX4) are presented as evidence of non-MHC sharing. However, ABCA7 is an established AD risk gene with no known MG relevance, and the other chr16 genes (ZNF668, CFAP119) have no established functional link to either neurodegenerative or autoimmune mechanisms. Their appearance may simply reflect coincidental sub-threshold associations in MG that happen to overlap with AD loci. Without functional validation or replication, these should be described as “putative” rather than implying confirmed sharing.

Point 26 – The case-control ratios are highly imbalanced: 71,880 vs 383,378 for AD (1:5.3) and 5,708 vs 432,028 for MG (1:75.7). Extreme case-control imbalance can bias LDSC heritability and correlation estimates (Grotzinger et al., 2022, Nature Genetics). The MG GWAS in particular has a very small case fraction. While the meta-analytic origin of these datasets makes rebalancing difficult, the potential impact on rg estimates and downstream analyses should be discussed.

Point 27 – The gene-based association methods (fastBAT, mBAT, mBAT-combo) aggregate all SNPs within ±50 kb of each gene, including common variants of uncertain significance, likely benign, and synonymous variants. Genes harbouring many common, non-functional SNPs in strong LD with neighbouring trait-associated regions could appear significant without containing any functional variant. Were genes dominated by neutral or benign variants excluded? If not, this source of potential false positives should be acknowledged.

Point 28 – The analyses use multiple reference panels and genome builds. Were all coordinates harmonised to the same build (hg19 or hg38) prior to cross-trait comparison? The gene-based GEC analysis uses NCBI gene definitions (build 37 / hg19), while some GWAS data may be in hg38. Coordinate mismatches could introduce false negatives. Additionally, no estimate of type II error rate is provided for the gene-level overlap analysis. Given the modest effect sizes involved, the study may have substantial power limitations to detect true shared genes, particularly outside the MHC. A formal power analysis for gene-level overlap detection would be informative.

Point 29 – Stouffer’s Z-score method for combining gene-based p-values (Section 2.9.1) assumes independence of the input p-values. However, genes in the MHC region are in extensive LD and are not independent. While GEC attempts to account for this, the combined Z-scores for MHC genes (Table 5: HLA-DQB1, BTNL2, TSBP1, HLA-DRA, etc.) may be inflated due to residual non-independence. An LD-aware p-value combination method, or at minimum a sensitivity analysis excluding MHC genes, would address this concern.

Point 30 – MR for complex polygenic traits with shared genetic architecture is susceptible to bias from: (a) weak instrument bias (F-statistic should be reported for each instrument set), (b) reverse causation (particularly relevant given the cross-trait genetic correlation), and (c) collider bias when conditioning on covariates. The authors cite adherence to STROBE-MR guidelines but do not state whether additional MR-specific guidelines (e.g., Burgess et al., 2019, JAMA) were consulted. F-statistics for the MG instrument set should be reported in the main text.

Point 31 – The GWAS-PW colocalisation analysis is performed only for AD–MG overall, not for AD–EOMG or AD–LOMG. Given that the LAVA analysis reveals substantially different local correlation patterns for EOMG and LOMG (e.g., LOMG shows stronger and more widespread signals, including non-MHC loci), subtype-specific colocalisation would add considerable value. Additionally, was any correction for multiple region testing applied across the 1,703 genomic regions analysed? The risk of over-fitting increases with the number of tested regions.

Point 32 – While the AD analysis includes a partial replication using the Lambert et al. GWAS, no independent MG replication cohort is used. The single MG GWAS (Braun et al., 2024) is the only available large-scale dataset, but this means all MG-side results rely on a single study with a comparatively small case count. This should be acknowledged as a limitation, and the authors should discuss how emerging MG GWAS (e.g., from biobank-scale efforts) might enable future replication.

Minor Concerns

Point 33 – The introduction’s presentation of AD pathogenesis (lines 64–78) omits α-synuclein co-pathology, TDP-43, and vascular contributions, which are increasingly recognised as part of AD heterogeneity. For a study investigating cross-disease genetic overlap, acknowledging that AD itself is genetically and pathologically heterogeneous is important.

Point 34 – The bubble plot in Figure 3b would benefit from a different visualisation strategy. Since both size and colour encode the same variable (–log10 pSMR), one encoding is redundant. A heatmap or dot plot with colour for tissue type and size for significance would be more informative.

Point 35 – The gene–drug interaction analysis (Section 2.10.1) is preliminary and speculative. Listing anticoagulants (warfarin via VKORC1) and immunomodulators (infliximab, adalimumab via HLA genes) as “potential therapeutic targets” for AD–MG overlap is a considerable leap from statistical genetics to clinical application. This section should be framed more cautiously.

Point 36 – All analyses are restricted to European ancestry. Given that both AD prevalence and MG subtype distribution differ across ancestries, the generalisability is limited. This is acknowledged but should be more prominently noted in the abstract.

Point 37 – The tissue-enrichment analysis (Section 2.4) uses only the LDSC-SEG approach with nominal P < 0.05 threshold. No FDR correction is applied, and alternative methods (e.g., MAGMA tissue enrichment) are not used for validation.

Point 38 – Section 2.5.1 is numbered as such, but Section 2.4.2 (line 267) appears with different numbering — the pairwise LAVA section is labelled “2.4.2” rather than “2.5.2.” Section numbering should be corrected throughout.

Point 39 – Were the analyses performed using consistent genome builds? Gene definitions use build 37, eQTL data from GTEx v8 are mapped to GRCh38, and GWAS may use either build. Explicit liftover procedures (or confirmation that all data are in the same build) should be described.

Point 40 – The discussion of “differential weighting” along the innate–adaptive immune axis (lines 670–674) is an interesting hypothesis but is based only on tissue-enrichment contrasts, which are indirect and qualitative. This should be presented as speculative.

Author Response

Reviewer 2

Adewuyi et al. present a multi-resolution investigation of shared genetic architecture between Alzheimer’s disease (AD) and myasthenia gravis (MG), integrating genome-wide correlation (LDSC), locus-level analysis (LAVA), SNP-effect concordance (SECA), cross-trait GWAS meta-analysis, colocalisation (GWAS-PW), bidirectional Mendelian randomisation (MR), gene-based analyses, summary-data-based MR (SMR), pathway enrichment, and gene–drug interaction mapping. The study leverages large-scale GWAS summary statistics for AD (~72K cases + 383K controls) and MG (~5.7K cases + 432K controls) of European ancestry. The authors report modest positive genome-wide genetic correlation (rg ≈ 0.11), predominantly MHC-driven locus-level overlap with some non-MHC signals (notably chromosome 16), limited MR evidence for a weak MG–AD causal effect, and convergence on immune-related pathways and genes. The analytical framework is comprehensive and technically competent, employing state-of-the-art methods across multiple genomic resolutions. However, I have significant concerns about the specificity of the findings, the interpretive framing, the reliance on the MHC region, and several methodological and reporting issues that should be addressed before publication. Below I detail these concerns.

Response: We thank the reviewer for the thorough summary of our study and for acknowledging the breadth and technical rigour of the analytical framework. We have carefully addressed the concerns raised below and revised the manuscript to improve clarity, interpretation, and reporting.

Major Concerns

Response: We thank the reviewer for this important observation. We agree that the current study was not designed to establish whether the observed overlap is specific to MG relative to other autoimmune disorders, and we did not perform a formal negative-control autoimmune comparison. Our objective was instead to characterise the magnitude, localisation, and heterogeneity of AD–MG genetic sharing within a biologically motivated disease pair. Importantly, however, the findings do not support a simple uniform AD-MG immune axis explanation. Across analyses, we observed substantial heterogeneity, including mixtures of concordant and discordant local correlations, subtype-specific differences between EOMG and LOMG, evidence for distinct causal variants across many MHC loci, and non-MHC signals supported across complementary analyses. Accordingly, our interpretation throughout the manuscript has been that the AD–MG relationship reflects modest, heterogeneous, and locus-specific overlap rather than broad genome-wide or uniformly shared immune architecture. We have nevertheless revised the discussion further to acknowledge that some components of the observed overlap may reflect broader immune-related mechanisms that are not unique to MG.

Response: We thank the reviewer for this detailed comment and agree that immune‑related signals within the MHC account for a substantial part of the locus‑, gene‑, and pathway‑level findings between AD and MG. We would like to clarify, however, that our discussion does not downplay these results. The statement that the genome‑wide genetic correlation persists after exclusion of the APOE and MHC regions refers specifically to the LDSC global correlation estimate and was intended to indicate that the modest polygenic correlation is not exclusively driven by a small number of canonical loci. This statement does not contradict the results implicating the MHC in the downstream analyses. Notably, our results demonstrate that the MHC contribution itself is not monolithic. Colocalisation analyses predominantly supported distinct causal variants (PPA4) across MHC sub‑regions, and local genetic correlation analyses identified both positive and negative correlations within different MHC segments, indicating substantial internal heterogeneity rather than a single uniform immune driver. This heterogeneity is a key feature of our interpretation and is stated in the discussion.

With respect to non‑MHC evidence, we note that contributions outside the MHC are more modest but extend beyond suggestive signals. Gene‑based analyses identified shared non‑MHC genes, and expression‑based SMR analyses, which provide a more direct test of putative regulatory relevance, prioritised multiple non‑MHC genes across chromosomes 1, 7, 11, 15, and 16, alongside the well‑supported chromosome 16 locus. These findings suggest modest, locus‑specific non‑MHC involvement that is biologically informative, even if not as extensive as MHC‑driven enrichment. Importantly, an absence of significant local correlation outside the MHC should not be interpreted as the absence of shared association, as heterogeneous or opposing effects, multiple causal variants, and limited power can attenuate local correlation estimates. To resolve the perceived narrative tension, the discussion now states that the AD–MG relationship is characterised by MHC-loci but internally heterogeneous architecture, together with modest, locus-specific non-MHC contributions, most convincingly supported by chromosome 16 and SMR‑prioritised regulatory genes. We believe this framing aligns the discussion closely with the results and avoids any implication that non‑MHC evidence rivals immune‑driven signals in scope, while still recognising its biological relevance.

Response: We note first that AD‑by‑proxy is already defined in the Methods (supplementary note). However, in response to this comment, we now include this definition in the main manuscript (methods). Importantly, we respectfully note that it would be inappropriate to interpret the SECA results in isolation. SECA is a directional SNP‑effect concordance test that is sensitive to sample size and association strength [2]. In our analysis, SECA was conducted using independent SNPs in dataset 1 selected via double LD‑clumping, thereby minimising correlation among instruments and reducing the influence of LD structure or proxy‑related artefacts. Given that the Lambert et al (clinically diagnosed AD GWAS) is substantially smaller than the primary AD GWAS, our interpretation that power likely accounts for the lack of SECA signal appears to be the most likely case. For example, the same Lambert dataset shows consistent (nominally significant) genome‑wide genetic correlation with MG in LDSC analyses, both with and without exclusion of the APOE and MHC regions. This observation suggests that shared genetic signals are detectable when assessed using methods appropriate for modest, polygenic effects. Accordingly, our conclusions do not rely on SECA alone, but on convergence across multiple complementary methods with distinct assumptions and sensitivity profiles. We have strengthened the discussion to make this integration more explicit. We also noted the merit of the likely impact of the AD-by proxy and clarified that SECA findings should be interpreted in the context of the full analytical framework rather than as a stand‑alone test of shared genetic architecture.

SECA findings should be interpreted in the context of the full analytical framework rather than as a stand‑alone test of shared genetic architecture (lines 242 – 244).

…most likely reflecting reduced statistical power, analytical resolution or sensitivity to association strength in the latter. While the inclusion of AD-by-proxy cases in the primary GWAS may also introduce broader signals, potentially contributing to this discrepancy, we consider this a secondary factor relative to the substantial difference in sample size, especially given that SECA is more sensitive to sample size (lines 674 – 689).

Response: As requested, we have revised the manuscript to ensure that the MR findings are consistently described as inconclusive or suggestive, rather than ‘modest’. In addition, the methodologies used to assess horizontal pleiotropy (MR‑Egger intercept, MR‑PRESSO, and HEIDI outlier detection) are now described in the main Methods section.

We conducted comprehensive sensitivity and further MR analyses [37, 39, 40, 65, 66, 70-72]. These included Cochran’s Q statistic to evaluate heterogeneity in SNP effects, single-SNP MR analyses to examine the consistency of causal estimates across individual IVs, and leave-one-out analyses to determine whether any single IV disproportionately influenced the overall results. We applied the MR-Egger intercept test to assess deviations from the assumption of no directional pleiotropy, where a significant departure from zero would indicate a potential violation. We also used the MR-PRESSO method, which detects and removes outlier variants contributing to pleiotropic effects [40]. In addition, we performed bidirectional GSMR analyses with the HEIDI-outlier test [39]. IVs were selected using both genome-wide significance (P < 5 × 10^-8) and suggestive (P < 1 × 10^-6) thresholds to improve instrument strength and coverage. (see Supplementary Note 1 for details) (lines 975 – 988).

Response: We clarify that the tissue and pathway enrichment analyses were performed for AD and overall MG, not specifically for AD–LOMG, and are based on genetic variation that primarily captures inherited susceptibility rather than age-dependent immune states such as immune senescence or inflammaging. Age itself does not enter the analyses directly, and immune-cell heritability enrichment reflects genetically regulated pathways potentially contributing to disease risk rather than immune activation acquired during ageing. While AD and LOMG both manifest later in life, the observed immune enrichment is more consistent with overlapping inherited liability to immune-related mechanisms (though not in a simple way as our study has shown) than with a uniform ageing-related immune background alone. Importantly, the pronounced locus-level heterogeneity, including non-MHC loci, opposing local genetic correlations, and evidence for distinct causal variants across multiple MHC sub-regions, is difficult to reconcile with a single global ageing-driven immune signal. In addition, the subtype-specific differences observed between AD–LOMG and AD–EOMG further support a more complex and heterogeneous genetic architecture than would be expected from general inflammaging alone. We nevertheless agree that age-related immune dysregulation provides important biological context for late-onset disorders and may interact with inherited immune susceptibility in shaping disease manifestation, even if it does not directly contribute to the shared germline genetic architecture interrogated in this study. We have therefore clarified this point in the revised discussion.

We added this to the discussion:

Although immune-cell enrichment and immune-related pathways may partly reflect broader ageing-related immune processes, these analyses are based on germline genetic variation and therefore primarily capture inherited immune susceptibility rather than immune activation acquired with age. The pronounced locus- and subtype-specific heterogeneity, including non-MHC signals, opposing local correlations, and evidence for distinct causal variants across MHC sub-regions, suggests that the observed overlap is unlikely to be explained by a single uniform ageing-related immune background alone, and instead reflects a more complex interplay between inherited immune susceptibility and age-related disease processes (lines 812 – 820).

Response: The Introduction situates MG within the broader context of autoimmune diseases linked to AD and does not imply that MG is uniquely associated with AD. We note that direct cholinergic involvement is not a general feature of autoimmune disorders. MG is biologically distinct in that it is defined by autoantibodies targeting nicotinic acetylcholine receptors, a system centrally implicated in AD pathophysiology and therapeutically targeted by acetylcholinesterase inhibitors in both conditions. This cholinergic synaptic involvement, together with epidemiological associations, therapeutic overlap, and reports of cognitive effects in MG despite its peripheral classification, provides a mechanistically specific rationale for focusing on AD–MG overlap rather than autoimmunity more broadly. Accordingly, the aim of this study was not to compare MG against all autoimmune conditions, but to provide a detailed genetic characterisation of the AD–MG relationship, which remains comparatively understudied at the genomic level despite its potentially informative neuroimmune–cholinergic context. To further clarify this rationale and avoid misunderstanding, we have made minor revisions to the introduction to contextualise MG relative to other autoimmune disorders without implying exclusivity.

Response: A sex-stratified genetic analysis was not performed primarily due to data and power limitations, particularly for MG. To the best of our knowledge, publicly available, well-powered sex-stratified MG GWAS summary statistics are currently limited. Similarly, although sex was included as a covariate in the original GWAS analyses, we did not identify publicly available sex-stratified summary statistics for the Jansen et al. AD GWAS among the datasets released with the original publication (https://vu.data.surfsara.nl/index.php/s/l7aiRr1UEgdoJfZ). Moreover, stratifying MG by sex, based on the currently available sample size, would substantially reduce statistical power and increase uncertainty, potentially yielding unstable estimates. Notably, our analyses capture average genetic effects across sexes, which remains a standard practice in cross-trait studies when sex-specific data are unavailable or underpowered. In response to the reviewer’s suggestion, we have acknowledged this limitation and noted that sex-stratified cross-trait analyses represent an important direction for future work as larger MG GWAS datasets become available. We believe this clarification appropriately contextualises the findings without over-extending inference beyond the available data.

Fifth, given the recognised sex differences in both AD and MG, the relationship between these traits may be sex-specific; however, we were unable to assess this in the present study owing to data limitations. Future studies using sex-stratified GWAS for both traits will be important to determine whether their shared genetic architecture differs by sex (lines 876 – 880).

Specific Analytical and Reporting Concerns

Response: We have revised the opening sentence of the Abstract to avoid redundancy with the Introduction.

Response: We have revised the wording to avoid implying a strictly unidirectional causal relationship and now state that cholinergic dysfunction in AD ‘is associated with’ loss of basal forebrain neurons.

Response: We agree that broader gut–brain immune interactions provide additional biological context. We have therefore revised the text to acknowledge emerging evidence implicating gut microbiome–mediated immune signalling along the gut–brain axis in AD-related neuroinflammation, alongside previous evidence of a shared genetic architecture between AD and gastrointestinal traits. We have added:

These shared biological features encompass both central and peripheral immune dysregulation, including gut microbiome–mediated immune signalling along the gut–brain axis, which has been implicated in neuroinflammation in AD [3-5]. Together with the reported genetic overlap between AD and gastrointestinal traits [6], this broader immune context raises the possibility of a more complex relationship between AD and MG [7-13] (lines 103 – 107).

Response: Observational associations between MG and AD may be influenced by factors such as healthcare utilisation, surveillance bias, and potential underdiagnosis within comparison populations. We also acknowledge that increased neurodegenerative risk in MG, if present, may not necessarily be specific to AD alone. However, the epidemiological findings were presented primarily as background context, rather than as evidence supporting disease-specific association or causality. Importantly, the primary aim of the present study was to investigate potential shared genetic architecture using GWAS-based approaches, which are less susceptible to many forms of ascertainment and healthcare utilisation bias associated with observational studies. We agree that future studies comparing AD with other dementia subtypes in the context of MG would be valuable for clarifying disease specificity and have noted this as an important direction for further research.

Similarly, future studies comparing AD with other dementia subtypes in the context of MG would be valuable for clarifying disease specificity (lines 880 – 882).

Response: We agree that cognitive dysfunction is not unique to MG. Our intention was not to present cognitive impairment in MG as disease-specific evidence of AD-related pathology, but rather as part of the broader neuroimmune context motivating investigation of the AD–MG relationship. Importantly, we noted that the reported cognitive impairments ‘do not necessarily indicate AD’ and that existing evidence remains ‘inconclusive regarding a specific relationship between AD and MG’. To further clarify this point, we have revised the introduction to acknowledge that cognitive dysfunction is common across chronic autoimmune conditions and may reflect broader systemic or neuroimmune mechanisms rather than AD-specific processes alone. We added:

Similar cognitive profiles have been described in other autoimmune and inflammatory conditions, suggesting that such impairments may reflect non-specific effects of systemic immune dysregulation rather than AD–specific pathology [14, 15] (lines 127 – 130).

Point 13 – Page numbering resets after Table 5.

Response: We thank the reviewer for noting this issue. The page numbering reset appears to be related to the journal template formatting rather than the manuscript content itself. We anticipate that this will be corrected during the typesetting stage.

Response: The statement in the Abstract referring to ‘modest polygenic overlap’ summarises the overall pattern of evidence across multiple complementary analyses, including genome-wide correlation, SNP effect concordance and gene-level overlap, rather than the LDSC genetic correlation results alone. In response to this comment, we made corrections by adding the following text:

Genome-wide analyses identified modest polygenic overlap between AD and MG overall, supported by nominally significant genome-wide correlation, SNP-level enrichment in the primary GWAS, and robust gene-level overlap. Evidence for genome-wide correlation was weaker and non-significant across MG subtypes (lines 41 – 45).

Response: To improve clarity and interpretability, we have revised the figure legend to indicate that the dotted line represents cell types showing nominally significant enrichment (P<0.05).

Response: Tables 1 and 2 summarise local genetic correlation estimates across LD-defined genomic regions rather than individual causal variants or genes. As such, adding functional annotations at the regional level would be ambiguous and potentially misleading. Similarly, the SNP-level associations reported in Table 3 do not necessarily represent causal functional variants, particularly within complex loci characterised by extensive linkage disequilibrium. Instead, biological interpretation was intentionally addressed through downstream integrative analyses, including gene-based testing, SMR, pathway enrichment, and gene–drug interaction analyses, where functional relevance can be evaluated more appropriately. In addition, the study workflow (Figure 1) was designed to illustrate how these complementary analytical layers contribute to biological interpretation across the study.

Response: As expected for loci within the extended MHC, local genetic correlation estimates can be modest in magnitude, reflecting extensive linkage disequilibrium and heterogeneous architecture rather than weak biological relevance. Based on how local genetic correlations are interpreted, the estimates referenced by the reviewer are modest in magnitude; these estimates are statistically significant and consistent with expectations for local correlation analyses of complex polygenic traits, especially within the MHC. Our manuscript has already interpreted these findings as modest, where appropriate, and we used cautious wording in our discussion.

Response: We note that the term (putative or consistent with-) ‘antagonistic pleiotropy' was used to characterise the observed pattern of both concordant and discordant local correlations across loci, rather than to imply a formally tested excess of directional heterogeneity beyond chance. Local genetic correlation methods such as LAVA are specifically designed to estimate locus-specific genetic covariance while accounting for local linkage disequilibrium structure. The presence of statistically significant positive and negative correlations across different loci, particularly within well-powered regions such as the MHC, supports heterogeneous local genetic architecture rather than uniform directionality. Importantly, these opposing effects were not interpreted in isolation, but in the context of convergent evidence from complementary analyses, including GWAS-PW results showing predominantly distinct causal variants within the MHC. Together, these findings support a heterogeneous, locus-specific architecture which is consistent with ‘antagonistic pleiotropy’. Permutation-based assessment of directionality heterogeneity is not standard practice in local genetic correlation studies and is not required for qualitative interpretation of locus-specific discordance.

Response: We have stated the threshold for ‘nominal significance’ (P < 0.05). We agree that nominal significance alone (P < 0.05) would not be sufficient to infer cross-trait involvement independently. However, this was not the basis on which variants were prioritised in our study. Specifically, the variants discussed were first identified through heterogeneity-aware cross-trait meta-analysis showing strengthened association evidence after meta-analysis, together with genome-wide significance in at least one trait. Nominal association in the secondary trait was then considered as supportive evidence within a broader interpretive framework incorporating m-values and BE p-values, which assess the likelihood of effects across one or both traits while accounting for cross-trait heterogeneity. Accordingly, the nominal threshold was not used as an arbitrary standalone filter, but rather as one component of convergent evidence supporting potential cross-trait involvement.

Response: We note that GWAS-PW was applied in this study as a regional colocalisation framework to distinguish broad patterns of shared versus distinct regional association, rather than as a high-resolution fine-mapping approach intended to resolve individual causal variants. Accordingly, the GWAS-PW findings were interpreted cautiously and in conjunction with complementary analyses, including local genetic correlation, heterogeneity-aware meta-analysis, and SMR results. Importantly, our interpretation of the MHC was consistent with the reviewer’s concern regarding complex regional architecture. Most MHC segments showed stronger support for distinct causal variants (high PPA4) rather than a single shared causal signal, reinforcing the conclusion that overlap in this region is heterogeneous and unlikely to reflect uniform variant-level sharing. The genome build for data used in our study is hg19. We have provided this information where appropriate in the manuscript.

Response: We thank the reviewer for this observation. The slightly higher effective-to-observed ratio for the overlap set reflects the fact that the GEC adjustment is determined by the correlation structure within each specific gene set rather than by the absolute number of genes alone. Because the overlapping gene set represents a distinct subset with its own LD and correlation characteristics, its effective proportion is not expected to match or necessarily fall below those of the individual trait-specific sets. In this case, the overlap set appears to contain slightly less correlated genes on average, resulting in a marginally higher effective-to-observed ratio (0.82 versus 0.79–0.80). The difference is small and reflects properties of the GEC estimation procedure rather than inflation of overlap significance.

Response: We agree that genes located within the extended MHC region should not automatically be interpreted as functionally immune-specific. Our classification of genes such as NOTCH4 and C6orf15 as part of the ‘MHC-clustered’ signal referred to their genomic localisation within the broader MHC-associated region rather than to a specific functional annotation or assumption of direct immune causality. We acknowledge that several genes within the MHC have pleiotropic or non-immune biological functions and that association signals in this region may partly reflect extensive LD with neighbouring variants. Importantly, our interpretation of the MHC throughout the manuscript emphasised regional complexity, allelic heterogeneity, and predominantly distinct causal variants rather than uniform immune-driven mechanisms. We have nevertheless clarified the wording to avoid any implication that all genes within the MHC-associated regions should be interpreted as canonical immune-effect genes. We added:

Genes located within MHC-associated loci were interpreted primarily in the context of regional genomic localisation and should not necessarily be considered functionally immune-specific, given the extensive pleiotropy and linkage disequilibrium structure of the region (lines 551 – 554).

Response: We thank the reviewer for this helpful suggestion. We agree that the original version of Figure 3b redundantly encoded the same information (−log₁₀ p_SMR) using both bubble size and colour. In response, we have revised Figure 3b to improve visual efficiency and interpretability. In the updated version, colour alone encodes −log₁₀ p_SMR, while bubble size is now uniform, thereby removing redundancy and clarifying the strength of the SMR signal across genes and tissues. We believe this revised presentation more clearly conveys the results and makes more effective use of visual channels.

Response: We agree that tissue‑specific heritability and pathway enrichment analyses rely on curated gene sets that may be uneven in coverage. We have noted this in the limitation section:

Sixth, well‑studied immune and neural cell types are more comprehensively represented in current databases; hence, tissue and pathway enrichment results should be interpreted in light of unequal annotation coverage across tissues (lines 886 – 889).

Response: We have intentionally framed these findings as putative rather than definitive shared loci. The presence of ABCA7 reflects its well-established association with AD, while the accompanying MG association was modest and interpreted cautiously. Similarly, loci on chromosome 16 were highlighted as candidate regions supported by convergent statistical evidence across complementary analyses, rather than by prior functional annotation linking these genes directly to MG or neurodegeneration. Importantly, the absence of previously established MG relevance for a gene does not preclude its identification in cross-trait analyses, as one purpose of such approaches is to detect potentially novel loci contributing to shared polygenic architecture. We therefore do not present these findings as functionally validated shared mechanisms, but rather as hypothesis-generating signals that warrant further replication and experimental investigation.

Response: We agree that the MG GWAS is relatively case-imbalanced, and this may reduce precision and power for LDSC and downstream cross-trait analyses. However, we would frame this as a limitation affecting statistical power and the conservativeness of the estimates rather than a source of bias. We have already noted in the manuscript that the MG dataset includes only ~5,700 cases, which limits power to detect smaller shared effects and should make the cross-trait estimates conservative (lines 865 – 868).

Response: In our analysis, fastBAT, mBAT, and mBAT-combo aggregated SNP-level association signals within a ±50 kb window around each gene while accounting for LD structure; therefore, gene-level significance should be interpreted as evidence of association burden rather than proof of a causal functional variant within the gene body. These approaches are designed to aggregate regional association signals rather than to prioritise variants based on predicted functional consequence. Importantly, our manuscript already notes that convergence at the gene level does not necessarily imply concordant variant-level effects, because aggregation can mask heterogeneity among individual SNPs.

Response: All analyses in this study were conducted using a consistent genome build (GRCh37/hg19), and no additional liftover procedures were required. Specifically, all GWAS summary statistics used for AD and MG analyses were provided in GRCh37/hg19 coordinates, and gene annotations for the gene-based analyses were also defined using GRCh37/hg19. Although GTEx v8 was originally generated on GRCh38, the SMR framework distributes pre-harmonised eQTL summary statistics mapped to hg19 for compatibility with GWAS integration analyses. Consequently, all cross-trait and transcriptomic integration analyses were performed within a single harmonised coordinate framework, minimising the risk of coordinate mismatch or associated false negatives.

Secondly, we acknowledge that the modest effect sizes and relatively limited MG case sample may reduce sensitivity to detect weaker shared gene-level signals, particularly outside the MHC region. This limitation is already discussed in the manuscript in the context of modest polygenic overlap and conservative cross-trait estimates. However, the gene-level analyses in this study integrate multiple complementary methods, and formal analytical power estimation for such multi-method overlap frameworks is not a standard practice and not within the scope of our study.

Response: The interpretation of MHC findings in this work is regional rather than gene-specific: the MHC genes highlighted in Table 5 represent a shared immune locus with convergent signals across multiple analytical frameworks. Importantly, the gene-level overlap testing that underpins our claims of excess cross‑trait overlap relies on the GEC framework, which accounts for LD and non‑independence among neighbouring genes. We further note that our principal conclusions do not depend on the MHC alone. Robust evidence for shared AD–MG architecture is also supported by non-MHC loci, including chromosome 16 regions showing concordant local genetic correlation, cross-trait meta-analysis significance, gene-based signals, and SMR-prioritised genes. Accordingly, any residual inflation of Z‑scores within the MHC would not alter the overall interpretation that shared genetic susceptibility between AD and MG is modest, and regionally concentrated.

Response: In our study, instrument selection used genome-wide significant SNPs with stringent LD clumping, and we conducted extensive sensitivity analyses, including weighted median, MR-Egger, MR-PRESSO, heterogeneity testing, leave-one-out analyses, and bidirectional GSMR. Importantly, we also performed bidirectional MR, which directly evaluates the possibility of reverse directionality. The main limitation in the MG→AD direction was the limited number of MG instruments, which we have already noted in the manuscript. We agree that reporting F-statistics would further strengthen transparency. We calculated SNP-level F-statistics for the MG instrument. All instruments showed F-statistics well above 10 (approximately 30.0 to 151), indicating that weak instrument bias is unlikely. We have added this information to the manuscript. We have briefly noted this information in the main manuscript. Supplementary Table 7 provides more information.

Response: GWAS-PW analyses were restricted to the overall AD–MG comparison because the MG subtype datasets, especially EOMG, had substantially smaller sample sizes and weaker local association signals, which may reduce the stability and interpretability of Bayesian colocalisation estimates. We therefore prioritised the overall MG analysis to maximise robustness of the shared-region inference. We further note that GWAS-PW is a Bayesian framework based on regional posterior probabilities rather than conventional hypothesis testing using frequentist p-values. Accordingly, standard multiple-testing correction procedures are not directly applicable in the same way as genome-wide association testing. To minimise false-positive interpretation, we used conservative posterior probability thresholds and interpreted GWAS-PW findings in conjunction with convergent evidence from independent analytical approaches, including LAVA, cross-trait meta-analysis, gene-based analyses, and SMR. Consequently, the highlighted shared regions were not inferred from GWAS-PW evidence alone.

Response: We agree that the absence of an independent large-scale MG GWAS for replication testing is an important data limitation. We have already noted throughout the manuscript that the relatively limited MG sample size likely reduces power and may yield conservative cross-trait estimates. We now further clarify that replication of the observed AD–MG overlap in future biobank-scale MG GWAS datasets will be important to confirm the robustness and generalisability of the findings, particularly for subtype-specific signals and non-MHC loci.

Minor Concerns

Response: Our study focuses on shared genetic susceptibility as captured by large‑scale GWAS, which, by design, integrates across this heterogeneity rather than resolving subtype‑specific pathology. We therefore limited the introduction to pathophysiological features most directly relevant to potential overlap with MG (e.g., immune and cholinergic mechanisms), while explicitly modelling heterogeneity at the genetic level using local correlation, locus‑specific analyses, and subtype‑stratified approaches. We believe this approach maintains conceptual accuracy while preserving focus and conciseness in an already extensive manuscript.

Response: We thank the reviewer for this suggestion. We agree that the original version of Figure 3b redundantly encoded −log₁₀ p_SMR using both colour and bubble size. In response, we have revised Figure 3b to adopt a clearer visualisation strategy: colour now encodes −log₁₀ p_SMR exclusively, while point size is held constant. This removes redundancy, simplifies interpretation, and improves comparability across genes and tissues, achieving the intended clarity without introducing additional complexity. We believe the revised dot‑plot representation addresses the reviewer’s concern and enhances the figure’s informativeness.

Response: We clarify that the gene–drug interaction analysis in Section 2.10 is framed as exploratory. We do not present anticoagulants or immunomodulators as validated therapeutic options for AD or MG. Rather, these examples illustrate established gene–drug relationships involving shared genes, thereby providing pharmacogenomic context and potential mechanistic insight. The manuscript does not claim clinical efficacy, and translational relevance is discussed cautiously in the context of hypothesis generation and prioritisation for future investigation. We also note that any therapeutic interpretation would require substantial functional, experimental, and clinical validation. We therefore believe the current framing is appropriately cautious.

Response: As requested, we have noted in the abstract that we used large European‑ancestry GWAS datasets.

Response: The tissue enrichment analysis was intended to provide biological context rather than serve as a primary inferential framework. Consistent with this premise, the manuscript defines enrichment at the nominal significance level (P < 0.05) and describes the findings as nominally significant throughout the results and Figure legends. We interpreted the findings cautiously and in conjunction with multiple complementary analyses and pathway enrichment. While alternative approaches such as MAGMA could provide additional validation, LDSC-SEG is itself a well-established method for tissue-specific heritability enrichment analysis. Importantly, the principal conclusions of the study do not depend solely on these enrichment results, but rather on convergent evidence across multiple analytical frameworks.

Response: We thank the reviewer for identifying this numbering inconsistency. The section numbering has been corrected throughout the manuscript.

Response: All analyses in this study were conducted using a consistent genome build (GRCh37/hg19), and no additional liftover procedures were required. Specifically, all GWAS summary statistics used for AD and MG analyses were provided in GRCh37/hg19 coordinates, and gene annotations for the gene-based analyses were also based on GRCh37/hg19 definitions. Although GTEx v8 was originally generated on GRCh38, the SMR Portal distributes pre-harmonised eQTL summary statistics mapped to hg19 for compatibility with GWAS integration analyses. Consequently, all GWAS, gene-based, and eQTL integration analyses were performed within a single harmonised coordinate framework.

Response: We agree that tissue enrichment signals alone are indirect and should not be interpreted as formal quantitative estimates of immune pathway dominance. However, we do not propose a novel mechanistic distinction, but rather contextualise our findings within the well-established immunogenetic frameworks of AD and MG. AD has consistently been linked to innate and myeloid‑driven immune processes, whereas MG is a prototypical adaptive immune disorder characterised by HLA‑mediated antigen presentation and lymphocyte involvement. Our results recapitulate this known polarity, so it is not speculative. We have clarified the text to emphasise that the observed ‘differential weighting’ reflects consistency with existing disease biology and should be interpreted as an integrative, hypothesis-generating synthesis rather than a definitive mechanistic claim.

Reviewer 3 Report

Comments and Suggestions for Authors

The present work investigates the extent to which Alzheimer’s disease and myasthenia gravis share genetic susceptibility and potential causal links by integrating evidence across multiple genomic scales. It distinguishes modest genome-wide overlap from more specific locus-level convergence while explicitly accounting for heterogeneity across MG subtypes. Using a multi-layered framework that combines heterogeneity-aware meta-analysis, colocalization, and expression-informed Mendelian randomization, the work prioritizes shared variants, genes, and loci, and identifies potential expression-mediated regulatory effects. These analyses are further complemented by tissue-specific and pathway-based approaches, enabling a biologically grounded interpretation of the shared and distinct mechanisms underlying the relationship between the two diseases.

A general comment is that the manuscript contains a substantial amount of valuable information; however, its presentation would benefit from improved organization. The authors could further improve the structure of the draft by more clearly separating results across analytical levels and providing clearer transitions between sections, which would enhance readability and help emphasize the key findings.

The results description is dense and, in some sections, mixes methods and results in one flow. For example, the description of the gene-level overlap analysis is difficult to follow due to the dense presentation of methods and results in a single paragraph. It would help to more clearly separate (i) how independent genes are defined, (ii) how gene-level associations are computed, (iii) how overlap is statistically evaluated. A short intuitive explanation such as comparing observed vs expected shared genes, would improve accessibility without sacrificing rigor.

Focusing on pairwise locus-level genetic correlation of AD with MG and MG-subtypes, the description of local genetic correlation results is difficult to interpret due to the dense reporting of loci, coordinates, and effect directions without sufficient conceptual framing. It would help to first summarize the key pattern, for example that AD–EOMG signals are largely confined to the MHC with mixed directions, whereas AD–LOMG shows a broader distribution including non-MHC loci, before presenting detailed locus-level results. Additionally, briefly clarifying the interpretation of positive versus negative local genetic correlations would improve accessibility for non-specialist readers. A schematic or summarizing sentence highlighting the contrast between MHC-driven heterogeneity and more distributed effects would strengthen clarity.

The quality and clarity of the figures could be improved.

Author Response

Reviewer 3

Response: We thank the reviewer for this thoughtful summary of the study. We appreciate the recognition of the study’s integrative multi-layered framework, the distinction between modest genome-wide overlap and locus-specific convergence, and the emphasis on subtype-specific heterogeneity and biologically informed interpretation.

Response: We appreciate the recognition of the breadth of information presented in the manuscript. In response, we revised the manuscript to improve overall organisation and readability by more clearly separating findings across analytical levels. Importantly, we have also strengthened the clarity of interpretation throughout the manuscript, explicitly distinguishing between genome-wide, locus-level, and gene-level evidence, and clarifying the relative strength and limitations of each. We have refined the narrative to better emphasise the key findings in the discussion, particularly the distinction between modest global overlap and stronger locus-specific signals, and to ensure consistent and cautious interpretation across sections. These revisions enhance both the structure and interpretability of the manuscript.

Response: We agree that the gene-level overlap section contains substantial methodological detail and that clearer separation of the analytical steps would improve readability. In response, we revised the relevant sections to more clearly distinguish: (i) the definition of approximately independent genes using the GEC framework, (ii) the computation of gene-level associations using fastBAT, mBAT, and mBAT-combo (methods), and (iii) the statistical evaluation of cross-trait overlap. We also added a brief intuitive explanation clarifying that the analysis evaluates whether the observed number of shared associated genes exceeds that expected by chance. We made corrections both in the results and methods sections to improve accessibility while preserving methodological rigour.

Response: We thank the reviewer for this constructive comment. We note that the manuscript already summarised the major subtype-specific patterns, including that AD–EOMG associations were largely confined to the MHC region with mixed local effect directions, whereas AD–LOMG demonstrated broader overlap spanning both MHC and non-MHC loci. To further improve accessibility and conceptual framing, we added a brief clarification explaining the interpretation of positive versus negative local genetic correlations and refined transitions, emphasising the contrast between MHC-driven heterogeneity and broader distributed effects across MG subtypes.

The quality and clarity of the figures could be improved.

Response: We have improved the quality and clarity of the figures. Indeed, we made use of the paid author services as recommended by the journal to improve the quality of our Figures.

Reviewer 4 Report

Comments and Suggestions for Authors

The article "Genome-wide and locus-level analyses reveal modest yet heterogeneous genetic sharing between Alzheimer's disease and myasthenia gravis" by Emmanuel Adewuyi and colleagues investigates whether Alzheimer's disease (AD) and myasthenia gravis (MG) share genetic liability. The authors use a broad framework, including LDSC, SECA, LAVA, cross-trait GWAS meta-analysis, GWAS-PW, Mendelian randomization, gene-based tests, SMR, pathway analysis, and drug-gene annotation. The paper is ambitious and generally clear. My main concern is that some interpretations are stronger than the data justify, especially for genome-wide signals, MR, and MHC-heavy results. Here are my points of criticism:

MAJOR points

1 The genome-wide evidence for shared genetic architecture needs softer wording. The LDSC correlation between AD and MG is nominally significant, but it does not pass the authors' Bonferroni threshold. The subtype analyses are also non-significant, and the SECA signal is not reproduced in the clinically diagnosed AD dataset. I do not think this invalidates the study, but it does mean that phrases implying robust or consistent genome-wide sharing should be toned down. The Abstract, Discussion, and Conclusion should distinguish nominal genome-wide evidence from the stronger locus-level observations.

2 The MR evidence for MG liability increasing AD risk is weak. The MG -> AD analysis uses very few instruments, the effect size is extremely small, and the finding does not replicate in the clinically diagnosed AD dataset. The authors should avoid causal-sounding language here and state clearly what unit the OR of about 1.01 refers to.

3 The colocalization results in the MHC need more caution. GWAS-PW is acceptable for a broad scan, but the MHC is not an ordinary locus: it has long-range LD, multiple independent immune signals, and complex haplotypic structure. In this setting, the difference between PPA3 and PPA4 can be unstable unless the analysis allows for multiple causal variants or includes conditional/fine-mapping follow-up. The Discussion mentions this, but the Results still read too confidently when describing shared versus distinct causal variants in the MHC. The authors should either treat the MHC colocalization results as descriptive or add stronger fine-mapping support.

4 The Bonferroni correction used for the pairwise LAVA analyses is not transparent. The Methods should say exactly how the 35, 24, and 24 tested loci were obtained, including the univariate filtering step and any excluded loci.

5 The cross-trait meta-analysis results are over-described as shared signals. The BE P-value tests for association in at least one study, not necessarily both traits. Also, several m-values in Table 3 are ambiguous or low for one trait, including the chr16 rs889555 signal and some MHC variants. These should not be presented in the same way as variants with convincing evidence in both AD and MG. The authors should separate signals supported by both traits from signals mainly driven by one trait. Table 3 should also include effect sizes and directions for both traits; otherwise the biological interpretation of sharing is incomplete.

6 The gene-based results should be interpreted by locus, not as a list of independent genes. Many top genes sit in the MHC or other dense LD regions, so several reported genes may reflect the same association signal. Stouffer's method combines P-values, but it does not prove that the same causal variant or mechanism is shared. The text should make this limitation explicit.

7 The pathway and drug-gene interpretation is too strong. The pathway enrichment appears heavily driven by HLA class II genes, so broad conclusions about immune, infection, and autoimmune pathways may mostly reflect the same MHC signal. The drug-gene analysis is also only a hypothesis-generating annotation. Links to immunomodulators, anticoagulants, or Notch inhibitors should not be framed as therapeutic prioritization without functional validation.

MINOR points

Section 2.4.2 should probably be 2.5.2.

Page 11, line 379: replace "which is not convincing".

Page 16, line 487: there is some confusion with the P-value ranges (D (0.001 < Pgene-AD > 2.67 × 10⁻⁶) or MG (0.01 < Pgene-MG> 2.67 × 10⁻⁶) ), I think the "<" should be ">". Or, if the authors mean that the p-values are in both cases greater than 0.01, it should be written in a simplified way without the 2.67 × 10⁻⁶.

Figure 4: The legend is too concise. Explain the relationship between the X-axis gtex datasets and the rest of plot.

Author Response

Reviewer 4

Response: We thank the reviewer for the thoughtful overview and constructive assessment of the study. We appreciate the recognition of the broad integrative framework employed, including genome-wide, locus-level, gene-based, and regulatory analyses. We also acknowledge the reviewer’s concerns regarding the interpretation of genome-wide signals, MR findings, and MHC-driven associations. In response, we carefully revised the manuscript throughout to further strengthen interpretive caution, more clearly distinguish modest genome-wide overlap from stronger locus-specific signals, and avoid overstating causal or disease-specific conclusions where the evidence remains preliminary or regionally heterogeneous.

MAJOR points

Response: We agree that genome‑wide evidence for AD–MG sharing should be interpreted cautiously. In response to similar concerns raised by another reviewer, we have already revised the Abstract, Discussion, and Conclusions to clearly distinguish modest, nominal genome‑wide overlap from the stronger locus‑ and gene‑level signals. We believe these revisions directly address the concern raised here.

Response: We revised the manuscript to avoid definitive causal-sounding language. We also clarified that the reported odds ratios refer to the effect of genetically predicted MG liability on AD risk per unit increase in log-odds of MG liability within the MR framework.

Response: We thank the reviewer for this comment. In response to related feedback from other reviewers, we have revised the manuscript to ensure consistently cautious language throughout. As a result, MHC colocalisation findings are presented as regional and interpretive rather than definitive, and our conclusions do not rely on MHC colocalisation alone. We believe the revised framing appropriately reflects our findings and cautious.

Response: We thank the reviewer for this comment. The Bonferroni denominators reflect the number of loci that advanced to bivariate testing following the standard LAVA univariate local heritability filtering step. As described in the Supplementary Methods and consistent with the program developers’ recommendations, we applied a relatively lenient univariate filter (P < 0.05) to retain sufficient loci for subsequent bivariate testing within each trait pair (see Supplementary Methods section). This resulted in 35 loci for the AD–MG analysis and 24 loci each for the AD–EOMG and AD–LOMG analyses, over which Bonferroni correction was applied. In response to this comment, we have clarified this workflow in the Methods section to improve transparency regarding how the number of tested loci and corresponding correction thresholds were determined. We added:

For the pairwise LAVA analyses, the number of bivariate tests was determined by the number of loci that passed the univariate local heritability filter (P < 0.05) in both traits under comparison. This resulted in 35 loci for AD–MG, 24 loci for AD–EOMG, and 24 loci for AD–LOMG, and Bonferroni correction was applied accordingly using these denominators.

Response: Response: We thank the reviewer for this important comment. We agree that BE p-values alone do not imply effects in both traits and that interpretation requires careful distinction between shared and trait-driven signals. In our manuscript, cross-trait meta-analysis results were interpreted using joint consideration of BE p-values and trait-specific m-values, which quantify the posterior probability of association in each trait. This framework allows clear differentiation between loci supported by both traits and those primarily driven by one trait with secondary evidence in the other. Variants with lower or ambiguous m-values in one trait (including rs889555 and the MHC variants) were interpreted cautiously and not presented as definitive shared associations. We also note that detailed SNP-level information, including effect sizes, directions, allele frequencies, and trait-specific statistics, is provided in Supplementary Tables 4–6. Table 3 in the main manuscript was intentionally designed as a concise summary highlighting cross-trait support rather than duplicating these detailed results. We believe this framework, together with the detailed quantitative information provided in the supplementary materials, appropriately reflects the strength and nature of the cross-trait evidence.

Response: As already stated in the manuscript, gene‑based aggregation can reflect shared underlying loci, and Stouffer’s method is used for signal prioritisation rather than to infer shared causal variants or mechanisms. Accordingly, gene‑level findings are consistently interpreted in conjunction with locus‑level analyses, colocalisation, and SMR results, and we explicitly note that convergence at the gene level does not imply variant‑level pleiotropy. We therefore believe this limitation is already appropriately acknowledged and addressed in the current text.

Response: As already stated in the manuscript, pathway enrichment results largely reflect immune‑centred architecture within the extended MHC and are discussed as providing biological context rather than evidence of distinct or disease‑specific pathways. Similarly, the gene–drug interaction analysis is framed as hypothesis‑generating and descriptive. We do not present links to immunomodulators, anticoagulants, or other compounds as therapeutic prioritisation, and we consistently note that any translational relevance would require substantial functional and experimental validation. We have provided limitations related to this analysis in the limitation section, We believe the current interpretation appropriately reflects the limitations of both pathway and drug–gene analyses.

MINOR points

Section 2.4.2 should probably be 2.5.2.

Response: Thank you for pointing out this mistake. We have corrected it.

Page 11, line 379: replace "which is not convincing".

Response: We intentionally retained this wording because the association was weak, inconsistent across sensitivity analyses, and not replicated in the clinically diagnosed AD dataset. We therefore believe it is important to clearly convey the limited strength of evidence for this finding.

Response: We thank the reviewer for highlighting this ambiguity. Our intention was to identify genes that reached genome-wide significance only in the combined p‑value analysis, while remaining below the genome‑wide threshold in the individual trait analyses, but still showing at least moderate evidence of association in both AD and MG. We have revised the text to clearly state these criteria, namely, P_{gene (AD and MG)} > 2.67 × 10⁻⁶, but P_gene-AD< 0.001 and P_gene-MG < 0.001, and simplified the notation to avoid confusion.

Figure 4: The legend is too concise. Explain the relationship between the X-axis gtex datasets and the rest of plot.

Response: To improve clarity, we have expanded the Figure 4 legend to explain the relationship between the tissue datasets shown on the x‑axis and the rest of the plot. We believe this revision improves interpretability without altering the underlying results. We added:

The horizontal-axis lists the individual eQTL reference datasets used in the SMR analysis, including whole-blood and brain meta-analysis resources (eQTLGen, BrainMeta) as well as tissue-specific brain eQTL datasets from GTEx. The vertical-axis shows genes prioritised by SMR as putatively mediating shared genetic associations between AD and MG. Each point represents a significant SMR association for a given gene in a specific eQTL dataset, indicating evidence that genetically regulated expression of that gene in the corresponding tissue may contribute to the observed cross-trait association. Point colours denote the chromosome on which each gene is located.

Reviewer 5 Report

Comments and Suggestions for Authors

Paper by Adewuyi et al. analyzes the possibility that a common genetic background might be involved in the Alzheimer’s disease - myasthenia gravis relationship evidenced by some clinical and epidemiological Observations. Their results, based on the analyses of a large array of public repository datasets indicates that some genetic region, genes and SNPs are shared by AD and MG. In particular some genetic markers of MG might be polygenic predisposing factors for AD but not vice versa. The methodological approach and results presented in the paper appear relevant and might be of interest for forthcoming pharmacogenetic/ -genomic research.

Some minor points necessitate attention:

Lines 615 – 619: Authors report that, at the locus level, late onset MG is stronger related to AD than early onset MG, with the involvement of MHC and non-MHC loci. A brief discussion on the role of non-MHC loci identified in AD pathogenesis might help to understand the biological and, maybe, clinical relevance of these findings.

Line 634: A brief discussion on the possible biological role of the rs889555 SNP of BCKDK gene in MG might be useful.

Author Response

Reviewer 5

Response: We thank the reviewer for the positive assessment of our study and for recognising the relevance of the methodological framework and findings. We appreciate the reviewer’s thoughtful evaluation and encouraging comments regarding the potential implications of this work for future pharmacogenetic and genomic research into the AD–MG relationship.

Some minor points necessitate attention:

Response: We thank the reviewer for this constructive suggestion. In response, we have added a brief discussion to further contextualise the non-MHC loci contributing to the AD–LOMG overlap. Specifically, we clarify that these non-MHC signals should be interpreted as heterogeneous and locus-specific genetic covariance rather than direct evidence of shared causal genes or pathways, particularly given the mixture of positive and negative local correlations observed across loci. We also highlight that these subtype-specific differences are biologically plausible considering established clinical and immunogenetic distinctions between early- and late-onset MG, now supported with an additional reference. Because local genetic correlation analyses identify regional concordance or discordance rather than causal biological mechanisms [1], we intentionally avoided extensive mechanistic or clinical interpretation of these loci.

Line 634: A brief discussion on the possible biological role of the rs889555 SNP of BCKDK gene in MG might be useful.

Response: We have added a brief contextual discussion of the rs889555 locus. We note that rs889555 maps to the BCKDK genomic region on chromosome 16, which is involved in branched-chain amino acid metabolism and has reported relevance to neuronal/metabolic regulation [2, 3]. We emphasise that the MG association at this locus is modest, accompanied by an ambiguous m‑value, and that this signal, together with the highly correlated variant rs59735493 (AD-associated with secondary effect in MR), reflects a single regional association rather than independent effects. Accordingly, we interpret this finding cautiously as putative cross-trait overlap at the locus level, rather than evidence of a shared causal mechanism or direct biological role in MG.

References

Werme, J., et al., An integrated framework for local genetic correlation analysis. Nature Genetics, 2022. 54(3): p. 274–282.
Harris, R.A., et al., Overview of the Molecular and Biochemical Basis of Branched-Chain Amino Acid Catabolism12. The Journal of Nutrition, 2005. 135(6): p. 1527S–1530S.
Sperringer, J.E., A. Addington, and S.M. Hutson, Branched-Chain Amino Acids and Brain Metabolism. Neurochemical Research, 2017. 42(6): p. 1697–1709.

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

The authors have improved the manuscript adequately.

Reviewer 4 Report

Comments and Suggestions for Authors

Despite the continuous use of "As already stated in the manuscript" in their response to my comments, I think the article only now has been expanded and improved enough to lift my doubts. And it is now robust enough to warrant publication.

Article Menu

Genome-Wide and Locus-Level Analyses Reveal Modest, Heterogeneous Genetic Sharing Between Alzheimer’s Disease and Myasthenia Gravis

Further Information

Guidelines

MDPI Initiatives

Follow MDPI