Two Eyes as Their Own Control: Selection-Robust Retinal Age Clocks

A retinal "aging clock" is a model that predicts a person's age from a photograph of the back of the eye. The gap between that prediction and the person's actual age is used as a cheap, non-invasive readout of how fast the body is aging. The most useful training data for these clocks sits in hospital eye-clinic archives. Those archives have a structural flaw: people are photographed because something is wrong with an eye, and the eye disease itself changes how old the retina looks. A clock trained on such data partly learns "who got referred to the eye clinic" rather than "who is aging fast." We propose to remove that distortion with information already in the archive: the person's other eye. Both eyes share one chronological age, one bloodstream, one genome, one referral history and one clinic, so any difference between the ages the model predicts for them must come from something local to one eye. We train the clock so that this difference is pushed toward zero. We then use the same left-versus-right contrast as an audit, measuring how much of a clock's output is driven by local, selection-linked disease. The audit needs no disease codes and no hand-picked "healthy" cohort.

The case for doing this now comes from one striking failure. A multimodal fundus-plus-OCT clock trained only on retrospectively chosen "healthy" eyes reached a test mean absolute error of 10.63 years. On eyes with age-related macular degeneration (AMD) the error rose to 13.35 years, with R² = −1.74 (Ludwig et al., 2026). The authors' fix was to feed the network the patient's diagnosis codes. That lowered the error to 6.00 years, but it lets the model read age from how common each diagnosis is in the archive, which is exactly the confounding we want to avoid.

Core Claim

The left-right pair works like a within-family comparison in epidemiology: everything shared by the pair, including whatever process selected this patient into the archive, cancels out of the difference between the two eyes. Our claim is that training a clock to agree with itself across a person's two eyes yields an age gap with three properties. First, it is insensitive to one-sided disease. Second, it stays stable when the mix of diseases in the training archive is changed. Third, it keeps its association with systemic health and mortality. Diagnosis-conditioned training and healthy-only training each fail at least one of these tests.

The second, separable claim is that the per-person inter-eye prediction gap gives a disease-label-free measure of how much a given clock leaks local pathology. That measure lets clocks trained on biased archives be compared without first assembling a clean reference cohort.

This differs from existing binocular networks. The Two-Stream Binocular Network, with its contrastive grading loss (Qian et al., 2021), and DMS-Net, which separates shared from discrepant inter-eye features (Huo et al., 2025), both use the pair to classify eye disease. They treat asymmetry as diagnostic signal to be amplified. We reuse their weight-shared, mirrored two-stream design. Our target, however, is a continuous systemic quantity, and our objective treats asymmetry as nuisance to be suppressed.

The proposal also differs from monocular retinal clocks. Yu et al. (2025) reached 2.79 years of error on healthy UK Biobank and Chinese cohorts and found a 3% mortality increase per year of gap. Ludwig et al. relied on outside filtering or labels to handle disease. Neither uses the second eye.

Research Program

Each eye image $x_e$, with $e \in \{L, R\}$ and the left eye mirrored to match the right, passes through a shared encoder and an age head $f$. For a person with chronological age $a$, training minimizes

$$\mathcal{L} = \sum_{e \in \{L,R\}} \ell\big(f(x_e), a\big) + \lambda\, \big|f(x_L) - f(x_R)\big| + \mu\, \mathrm{Var}\big(f(x_L) - f(x_R)\big),$$

where $\ell$ is the per-eye age loss. We will use the label-distribution loss of Yu et al. so the comparison with their clock is fair. The term weighted by $\lambda$ penalizes disagreement between the two eyes. The batch-level variance term weighted by $\mu$ discourages the model from moving both eyes' predictions in a correlated but disease-dependent way.

Because the label $a$ is identical for both eyes, the consistency term cannot remove true bilateral aging signal. It can only remove features that differ between the eyes. The deployed age estimate is the mean of the two outputs.

The backbone will be RETFound, which held its advantage over ImageNet-pretrained networks on subtle systemic signals in small-data settings (Yeo et al., 2025). We will repeat the main results with ResNet-50, because that study found the two comparable on large datasets.

The audit statistic is the regression slope of the inter-eye prediction gap on inter-eye differences in recorded disease. We estimate it only on discordant pairs, where one eye has a diagnosis and the other does not, and we use it only at evaluation, never in training. A clock with no local-disease leakage has a slope near zero.

Two known limits shape the design. The first is natural asymmetry: healthy eyes are not identical (Fineide et al., 2022), so too large a $\lambda$ could discard real signal. We therefore sweep $\lambda$ and report the inter-eye gap on disease-free pairs as the floor. The second is symmetric disease: when both eyes are affected, the contralateral control collapses (Chen and Liu, 2023). This applies to much diabetic eye disease and to bilateral AMD, and it is a real constraint rather than a solved case. We report bilateral-disease pairs as a separate stratum where we do not expect gains, so the method's scope is stated honestly.

Baselines

The naive reference is a single-eye clock trained on all clinic eyes with no disease information. It scores each eye independently and reports the per-person mean. This baseline shows how badly an unadjusted retrospective clock behaves.

The first strong competitor is healthy-only training, which is Study 1 of Ludwig et al. and also the regime of Yu et al.. Ludwig et al. report a test MAE of 10.63 years and an AMD-subset MAE of 13.35 years (R² = −1.74). Yu et al. report an MAE of 2.79 years on healthy cohorts.

The second strong competitor, and the one most likely to look best on raw error, is diagnosis-conditioned training (Ludwig Study 2). It reports a test MAE of 6.00 years and an AMD-subset MAE of 5.43 years.

All baselines use the same backbone, the same images, the same split by patient, and the same hyperparameter search budget, with 20 configurations each. For diagnosis conditioning, the one-hot codes are concatenated exactly as Ludwig et al. describe.

The key ablation sets $\lambda = \mu = 0$ while keeping the two-eye averaging. This isolates whether training-time agreement matters beyond test-time pooling. We also include a binocular-architecture baseline: the TSBN two-stream network retrained with an age-regression head instead of its grading loss. This checks whether a fused two-eye model learns invariance on its own without the explicit penalty.

Beating diagnosis conditioning is not defined by mean absolute error, where it may win by reading prevalence. It is defined by three outcomes. Our audit slope must be lower. Our age-gap association with comorbidity and mortality must change less across the selection stress test below. And our error on discordant-disease pairs must come within one year of our error on disease-free pairs.

No reported result was found on Lacuna for age prediction on ODIR-5K, or for any bilateral retinal age clock.

Why not just…?

Why not just take the younger-looking eye, or average the two eyes, at test time? This is the most serious threat. With one-sided disease that pushes predictions older, taking the minimum of the two eyes' predictions already removes most of the bias. We will include minimum-of-two and mean-of-two as baselines. If minimum-of-two matches consistency training on the audit slope and the stress test, we will report that the cheap heuristic suffices. The contribution then shifts entirely to the label-free audit and the stress-test protocol.

We expect consistency training to win for two reasons, both of which the experiments test. First, a minimum-of-two estimate is biased downward on disease-free pairs, because the minimum of two noisy estimates is systematically low. Second, the minimum discards disease that does not shift predicted age in a fixed direction, such as myopia, which may make eyes look younger.

Why not just condition on diagnosis codes, as Ludwig Study 2 did? Conditioning lowers error, but codes reflect the archive's referral and coding practice. A clock using them inherits whatever diagnosis prevalence by age the archive happened to have. The selection stress test changes exactly that prevalence. A conditioned clock's outputs should shift with it, and ours should not. Codes are also often missing or inconsistent across eras in retrospective data, and our method needs none at deployment.

Why not just reweight the cohort with inverse probability of selection? Reweighting balances only recorded factors. Physicians' reasons for ordering imaging are largely unrecorded, a limitation the selection-bias literature in this file stresses repeatedly. The within-person contrast cancels any selection factor shared by both eyes, recorded or not. We will run reweighting on recorded age, sex and diagnosis as a further baseline, and we expect it to help on prevalence shifts but not on the audit slope.

Why not just filter out diseased eyes with a classifier? This is healthy-only training made automatic. It inherits the Study 1 failure when deployed on the clinic population, and it removes the very patients whose systemic aging matters most.

Proposed Experiments

The development cohort is ODIR-5K, a clinic-collected set of paired fundus photographs from 5,000 patients with per-eye diagnoses across eight classes, used by Huo et al.. We will use the patient ages distributed with ODIR-5K, after first confirming that this field is present in the release. We will seek access to STARR (Ludwig et al.) or a comparable institutional repository. That would allow direct comparison against the Study 1 and Study 2 numbers and an evaluation against the Charlson Comorbidity Index.

UK Biobank serves as the less-selected population reference, with paired fundus images and mortality linkage (Yu et al.). We will report error overall, on disease-free pairs, on discordant pairs and on bilateral-disease pairs. We will also report the audit slope.

The decisive check is a controlled selection stress test inside UK Biobank, where the unselected population gives a ground truth. We draw training subsets with selection probability that depends on eye disease and age, mimicking clinic referral at several strengths. We train every method on each subset and evaluate on a fixed unselected test set.

A method is selection-robust if two quantities stay flat as selection strength increases. The first is the hazard ratio of all-cause mortality per year of age gap; Yu et al. found roughly a 3% increase per year in unselected data. The second is the audit slope. We predict a clear ordering in how much these quantities drift: diagnosis conditioning drifts most, the naive clock next, minimum-of-two and reweighting less, and consistency training least.

A final transfer test trains on clinic-collected ODIR-5K and evaluates on UK Biobank mortality. This asks whether an age gap learned from a biased archive still carries population-level risk information. A gap that carries clinic referral rather than aging should lose its mortality association in this transfer, and that is what we expect the diagnosis-conditioned baseline to show.