Do Microbiome Genetic Instruments Age? Succession-Aware Causal Inference Across Ancestries

When researchers want to know whether the gut microbiome causes a disease, they often use Mendelian randomization — a technique that treats genetic variants as a natural experiment, exploiting the fact that genes are shuffled at conception and so act like a randomized treatment assignment. This only works if each genetic variant is a valid "instrument": strongly linked to the microbial feature it stands for, and influencing disease only through that microbe. Two bodies of evidence now threaten both assumptions at once. First, the microbial community itself is not static: it follows a structured developmental trajectory across host life, including an abrupt functional turnover in mid-life around ages 38–43 Selecting age-related functional characteristics in the human gut microbiome and a collapse of fiber-fermenting Bifidobacterium between ages 40 and 60 Age-related changes of microbiota in midlife associated with reduced saccharolytic potential: an in vitro study. Second, the host's genetic effect on the microbiome is itself age-dependent: the lactase (LCT) locus — the single strongest host-genetic anchor of gut composition — barely acts in children and strengthens in adults as intestinal lactase declines Large-scale association analyses identify host factors influencing human gut microbiome composition. And because the lactase-persistence allele is common in Northern Europeans but rare elsewhere, the allele frequencies that make these instruments work are ancestry-specific.

Nobody has put these facts together. Every published microbiome Mendelian randomization study, including Association of gut microbiome with risk of intracranial aneurysm: a mendelian randomization study, treats the genetic–microbiome link as a fixed, life-long, Europe-wide property; its authors explicitly flag both ancestry bias and the impossibility of age-stratified checks as unresolved limitations. My claim is that instrument validity for the microbiome is not a constant but a function of host developmental stage and population ancestry, and that we can measure this function directly, then rebuild microbiome causal discovery around it.

Core Claim

The strength and validity of host-genetic instruments for the microbiome vary systematically over the host developmental clock and across ancestral populations, in a predictable direction: instruments discovered in mixed-age European cohorts lose instrument relevance (their F-statistics, a standard measure of instrument strength, fall toward or below the conventional threshold of 10) in age bins and ancestries where the underlying host physiology differs. We will construct an age-by-ancestry atlas of instrument strength, use invariance-based causal discovery to separate the portion of microbial succession that is functionally conserved across populations from the portion that is population-specific, and show that standard predictive evaluation hides this breakdown while formal transportability testing exposes it. If the atlas shows no significant heterogeneity, the premise is wrong and the field's static assumption survives — that is the falsifiable stake.

Research Program

The program has four parts, each reusing an existing technique in a new setting. The first reanalyzes the MiBioGen consortium data — 18,340 people with both genotypes and fecal 16S profiles across 24 cohorts in North America, Europe, Israel, and South Korea Large-scale association analyses identify host factors influencing human gut microbiome composition — binning individuals by age window and ancestry and estimating, per cell, the instrument strength of the 31 genome-wide significant loci, with the LCT–Bifidobacterium pair as the anchor test case. This extends what that consortium observed in passing (an age interaction it never modeled continuously and never validated in its non-European cohorts). Because extraction protocol alone explained roughly 29% of between-cohort variance in that data, every cell estimate will carry a batch-sensitivity check.

The second part moves from taxonomy to function. Across populations the specific bacterial genera filling each metabolic niche differ — only 9 of 410 genera appear in over 95% of MiBioGen samples — yet the metabolic handoffs of succession, such as infant bifidobacteria converting maternal milk sugars into the substrates that butyrate producers need Trophic Interactions of Infant Bifidobacteria and Eubacterium hallii during L-Fucose and Fucosyllactose Degradation, appear conserved. So we will model succession on the 85,364 shotgun metagenomes compiled by Self-Supervised Representation Learning for Microbiome Improves Downstream Prediction in Data-Limited Settings and Cross-Cohort Generalizability using functional gene families rather than taxa, treating each cohort-by-age-window as an "environment" and running Invariant Ancestry Search — the method from Invariant Ancestry Search that takes the union of minimally invariant sets to recover causal ancestors where the more conservative intersection approach returns nothing — to find functional features whose relation to age holds across environments. Validation targets are known in advance: the mid-life decline of CbiN, the cobalt transporter linked to vitamin B12 biosynthesis, and the loss of saccharolytic capacity documented by Selecting age-related functional characteristics in the human gut microbiome and Age-related changes of microbiota in midlife associated with reduced saccharolytic potential: an in vitro study.

The third part builds a transportable functional age clock under two hygiene rules the literature has proven necessary but never combined. Doppelgänger filtering removes near-identical sample pairs that inflate learned-model accuracy by 15–30 percentage points Detecting and mitigating doppelgänger bias in microbiome data: impacts on machine learning and disease classification, and ancestry calibration — the post-hoc approach of Ancestry Calibration of Polygenic Risk Scores Improves Risk Stratification and Effect Estimation in African American Adults — replaces covariate adjustment, which that paper showed manufactures "statistical ghosts" when paired with uncalibrated scores. Evaluation uses the two-stage hypothesis testing framework of Testing Generalizability in Causal Inference, which proves that minimizing prediction error does not establish causal transportability under population shift.

The fourth part is a consequence audit: taking the taxa that Association of gut microbiome with risk of intracranial aneurysm: a mendelian randomization study implicated — for example Streptococcus at odds ratio 5.19 and Oscillospira at 0.37 — and asking, via the atlas, in which age-by-ancestry cells those instruments retain strength. The point is not to overturn any single claim but to quantify how much of the microbiome-MR literature rests on cells never tested.

Baselines

The "do nothing" reference is standard epidemiological practice: pool all individuals, include the top ancestry principal components as linear covariates, and fit genus-level regressions and a random-forest age clock on raw abundances. It is the strongest competitor on convenience and acceptance, and it is exactly the configuration Ancestry Calibration of Polygenic Risk Scores... showed to be unstable — entering ancestry alongside uncalibrated scores produced artificial associations where none existed — so beating it means demonstrating stable effect estimates across held-out ancestry strata where the pooled model shows reclassification-level distortion, using that paper's own diagnostic. The strongest existing method for cross-population microbiome prediction is the self-supervised embedding pipeline of Self-Supervised Representation Learning for Microbiome..., which raised 100-sample age prediction from $r = 0.06$ on raw species abundances to $r = 0.14$ and improved cross-cohort generalization across countries by up to 81%. We will run it ourselves on the same 85,364 metagenomes, the same cohort splits, and an equal tuning budget, and we beat it only if our functional clock matches its cross-cohort age-prediction correlation while additionally passing the formal transportability test it was never given and yielding interpretable invariant features rather than black-box embeddings. For the mid-life transition classifier specifically, the reference is the support-vector machine with TF-iDF feature selection of Selecting age-related functional characteristics in the human gut microbiome, which reported an AUC of approximately 67% at the age-43 cutoff; matching or exceeding that on a doppelgänger-filtered, multi-cohort split is the bar. Finally, two ablations isolate the proposal's key ingredients: swapping Invariant Ancestry Search for Invariant Causal Prediction, which on real biological perturbation data yielded 8 invariant pairs (6 true positives) against IAS's 23 (7 true positives) Invariant Ancestry Search and is expected to return empty sets here; and removing the doppelgänger filter, where we expect inflated transfer metrics that collapse under the transportability test.

Why not just…?

Why not just pool everything and add ancestry PCs as covariates? This is the default, and it is precisely the configuration Ancestry Calibration of Polygenic Risk Scores... disproved for scores with ancestry-shifted distributions: the covariate trap produced unstable estimates and a spurious ancestry–height association that vanished under proper calibration, with 33.6% of top-decile diabetes-risk classifications changed on calibration. We run it as the pooled baseline anyway, and the experiment that settles it is whether its per-stratum effect estimates remain stable when strata are held out — the calibration literature predicts they will not.

Why not just train a random forest on species abundances and check cross-cohort accuracy? Two documented failures block this. In small-data regimes raw-abundance models achieved near-zero age prediction ($r = 0.06$) Self-Supervised Representation Learning for Microbiome..., and apparent accuracy of such models is inflated by 15–30 percentage points by doppelgänger leakage Detecting and mitigating doppelgänger bias.... More fundamentally, Testing Generalizability in Causal Inference proves prediction metrics cannot certify transportability. Our unfiltered, uncalibrated random forest is included as a baseline precisely to show how much of its transfer performance is leakage.

Why not just apply Invariant Causal Prediction across the ancestry cohorts? It is the obvious off-the-shelf invariance tool, but it intersects invariant sets across environments and returns empty sets when environments differ strongly and interventions are sparse — exactly the multi-ancestry, observational setting here. On the yeast deletion benchmark it recovered 8 candidate pairs versus IAS's 23 Invariant Ancestry Search. We run it as the ablation; if it does not return an empty set on our data, that would itself be a striking finding.

Why not just run age-stratified MR separately in each ancestry group, with no new machinery? This is the most serious alternative, and part of it — the atlas — is exactly that analysis, which is why the atlas stands as an independent deliverable. But stratification alone cannot do the rest: the strata are sparse (MiBioGen's non-European cohorts are a minority of 18,340 people), it operates on 16S taxa that do not transfer across populations (9 core genera out of 410), and it offers no formal statement about which findings transport. The invariance machinery, the functional feature space, and the transportability test are what convert a collection of stratum-specific estimates into a claim about conserved succession. If the plain stratified analysis matches the full pipeline's conclusions everywhere, the added machinery is unnecessary and we will say so.

Proposed Experiments and Decisive Checks

Experiment one builds the atlas on MiBioGen, holding out the East Asian and Middle Eastern cohorts entirely for validation: estimate per-cell F-statistics for the LCT instrument and the other significant loci, and test heterogeneity across cells. The decisive number is whether instrument strength for LCT→Bifidobacterium crosses the F > 10 relevance threshold between age bins within ancestries, and whether the adult effect detected in Europeans at $P = 1.28 \times 10^{-20}$ replicates in the held-out non-European adult cells. Experiment two runs the invariance search on the 85,364 metagenomes with environments defined by cohort and age window, training on the US and Israeli cohorts and testing transfer to the Dutch cohort, reporting IAS yield, ICP yield (expected empty), and whether the recovered invariant set contains the known CbiN and saccharolytic markers. Experiment three trains the functional clock under each hygiene condition and evaluates with the two-stage transportability test; the pre-registered comparison is against the self-supervised baseline's reported small-data age correlation of $r = 0.14$ and its up-to-81% cross-cohort improvement, on identical splits. Experiment four audits the intracranial-aneurysm instruments cell by cell. No reported result exists on Lacuna for cross-ancestry age-stratified microbiome instrument validity, which is the gap; if experiment one returns null heterogeneity, the proposal's premise fails cleanly and the static-instrument practice is vindicated — an outcome worth publishing either way.