Do Domain-Robust Retinal Vessel Models Erase the Alzheimer's Signal?

Retinal imaging is one of the few cheap, non-invasive windows onto brain health. The retina grows out of the same embryonic tissue as the brain, and in Alzheimer's disease its smallest blood vessels thin out. A meta-analysis of optical coherence tomography angiography (OCTA, a scan that images capillary blood flow in the retina) reports vessel density drops of about 1.1 to 1.6 points in patients compared with controls (Jin et al.). That signal is small, and it only helps screening if a vessel-segmentation model can measure it on whatever scanner and protocol a local clinic happens to own. The domain-generalization literature has made such models far more robust across devices and even across imaging modalities. But it has judged success by Dice overlap with healthy-anatomy masks. Some of its most effective tools work by filling in broken or missing vessels: learned shape priors that bridge gaps, and augmentations that push the model toward canonical vessel geometry. In AD, missing capillaries are the disease signal.

This note proposes to test that tension directly and then fix it. The core claim is that a model's robustness to domain shift should be measured by whether a known change in capillary density survives the trip across domains, not by Dice. We will build a controlled benchmark that injects graded, realistic capillary dropout into real OCTA and fundus images. We will then measure how much of the injected density loss each method recovers on unseen scanners and protocols. Finally, we will train a gap-correcting segmenter that learns to tell apart "the model missed a vessel" and "there is no vessel here." If current methods compress disease-scale density differences, a Dice-optimal model is the wrong thing to certify for dementia screening, and the field needs a different yardstick.

Core Claim

Two kinds of domain-generalization method plausibly bias the downstream biomarker toward healthy values under domain shift. The first is error correction with an anatomical prior, as in ErrorNet. ErrorNet trains a variational autoencoder on ground-truth masks and learns to repair "non-intuitive gaps." The second is canonicalization of vessel geometry, as in the Vector Field Transformer and AADG. The bias would make true dropout harder to see precisely on the out-of-distribution devices where accessible screening happens.

The quantity we care about is the attenuation factor

$$\beta_d = \frac{\hat{\Delta}_d}{\Delta},$$

where $\Delta$ is the true reduction in vessel density injected into an image, and $\hat{\Delta}_d$ is the reduction the pipeline measures on target domain $d$. A value of $\beta_d = 1$ means the disease-scale difference is preserved. A value $\beta_d < 1$ means the model shrinks it. At a true difference of about 1.1 to 1.6 density points, a $\beta$ of 0.5 would cut the effective AD-vs-control effect size in half. That translates directly into lost screening sensitivity.

We predict that $\beta$ and Dice come apart. Methods with higher cross-domain Dice may show lower $\beta$, especially on the parafoveal and deep-plexus regions that matter most.

How This Differs From Prior Work

Three papers supply the methods we stress-test. ErrorNet trains on 20 CHASE fundus images and reaches an average Dice of 71.0 on four unseen fundus datasets. VFT converts images to a Hessian-derived vessel-orientation field and transfers from fundus to OCTA at Dice 0.7602 on ROSE and 0.7876 on OCTA500. AADG searches over colour-space augmentations that maximize a Sinkhorn distance, an optimal-transport measure of how different two distributions are, and lifts fundus-to-OCTA Dice from 2.75% to 56.18%. None of these papers extracts a clinical density biomarker, and none asks whether pathology survives their corrections. Our work neither proposes a better Dice method nor re-runs these methods on new datasets. It asks a different question of them, and adds one training ingredient that targets the failure we expect.

Jin et al. motivates the effect sizes and the regions we measure. It also motivates the protocol axis: 3×3 mm scans show lower heterogeneity than 6×6 mm scans, so protocol is itself a domain shift that corrupts the biomarker.

INPUTADAPTER supplies the deployment constraint. It argues that certified clinical predictors have frozen weights, and it adapts inputs rather than the model. That frames our question as "what should be certified." It also offers a comparison point, discussed below.

Research Program

The first component is a known-effect injection benchmark. On OCTA images with expert vessel masks (ROSE and OCTA500) and fundus images (DRIVE, CHASE, STARE, HRF, ARIA), we remove capillary segments from the ground-truth mask. We then erase them from the image by inpainting local background texture sampled from nearby avascular tissue. Removal rates are set to produce density reductions from 0 to about 3 points, bracketing the meta-analytic range, and are concentrated parafoveally and around the foveal avascular zone. The realism of the injected images is checked in two ways. A classifier must fail to distinguish inpainted patches from native avascular patches. Graders must fail to tell them apart in a blinded test.

Each method is then trained on one domain and applied to the injected images of the other domains. We compute $\beta$ per domain, per region, and per injection level, alongside Dice. Domains include fundus→OCTA transfer and within-OCTA transfer across datasets. Where the file's datasets allow a protocol split, we also transfer across protocol. Otherwise we simulate 6×6 mm acquisition from 3×3 mm scans by degrading resolution and adding projection-style artifacts. This simulation is disclosed as a limitation.

The second component is dropout-aware error correction. ErrorNet's corrector is trained only on pairs where the image contains a vessel that the predicted mask lacks, so it learns that gaps are always errors. We add a second kind of training pair: the injection pipeline has truly removed the vessel from the image and from the target. The corrector is penalized for bridging these. A density-consistency term also ties the measured density on an injected image to its known value. The intended effect is that the corrector conditions on image evidence of absence rather than on shape plausibility alone. We apply the same pairs as extra augmentation for VFT and AADG to see whether the ingredient helps across method families.

The third component is a clinical check, which the file cannot supply. No OCTA dataset with AD labels appears in the research file. The meta-analysis pools nine studies of 20 to 140 subjects. Clinical validation therefore requires partnering with a group holding OCTA scans labelled for AD and controls, ideally from two devices or protocols. There we would test whether higher $\beta$ on the synthetic benchmark predicts a better cross-site AD-vs-control effect size. Until then, the synthetic benchmark is the main contribution. We will not claim diagnostic accuracy without that data.

Baselines

The naive reference point is a Residual UNet trained on the source domain with standard augmentation and applied directly. Hu et al. report Dice 0.6705 for this model on DRIVE→ROSE. We also include a trivial "measure nothing" floor: classical Frangi-style vesselness thresholding with a per-image threshold. It has no learned prior and therefore should not hallucinate vessels, though it will be noisy. This floor tells us whether learned methods add or subtract biomarker fidelity relative to the simplest possible measurement.

The strongest existing domain-generalization method on Dice is VFT with EnhanceNet. Hu et al. report Dice 0.7602 on ROSE and 0.7876 on OCTA500, against an in-domain ceiling of 0.8200. It is the strongest competitor because it comes closest to supervised performance under modality shift. Its orientation-field canonicalization is also a plausible source of attenuation.

AADG is included because its 56.18% fundus→OCTA Dice lets us check whether low Dice and low $\beta$ travel together.

ErrorNet is the direct parent of our ingredient. It reports 71.0 average cross-domain Dice from CHASE.

All methods are run on identical source and target splits and the same backbone where the architecture permits. Each gets the same hyperparameter-search budget, selected on a source-only validation set, and all are reported over five seeds. For $\beta$ there is no reported result found on Lacuna for any of these methods, so every $\beta$ value will be newly measured.

The key ablation isolates the dropout-aware pairs. We compare ErrorNet with and without them, and VFT with and without them, at matched training steps. Beating a baseline means raising $\beta$ toward 1 on held-out domains, with confidence intervals that exclude the baseline's value, while losing no more than about one Dice point.

Why not just…?

Why not just pick the model with the best cross-domain Dice and compute density from its masks? This is the default and a real possibility. If Dice and $\beta$ are tightly correlated across methods and domains, the proposal's premise fails, and we will report that as the result. The injection benchmark measures exactly this correlation. Nothing in the file shows Dice predicting biomarker fidelity: all three domain-generalization papers stop at Dice. And ErrorNet's stated goal of bridging gaps gives a concrete mechanism by which the two could diverge.

Why not just harmonize the density numbers statistically, for example by re-centering each site's values against its own controls? This is the most serious threat. It can remove a constant offset between devices cheaply, and it may beat a sophisticated segmenter. It has two limits, though. It needs labelled controls at every new site, which defeats cold-start deployment to a primary-care clinic. And it cannot undo attenuation: if a model compresses a 1.5-point difference to 0.7, shifting the mean does not restore the gap. We will run site re-centering on top of every segmenter. Separating offset (fixable by re-centering) from slope (not fixable) is the point of reporting $\beta$ as a ratio.

Why not just adapt the inputs to the certified model, as INPUTADAPTER does? INPUTADAPTER matches fine-tuning on ICU data, but it needs labelled target cohorts, and it optimizes the frozen model's task loss. If that loss is Dice-like, the adapter would inherit the same blindness to dropout. We treat it as complementary rather than competing. An image-space adapter trained on our injected pairs is a secondary experiment, but the adapter still needs the right objective, and supplying that objective is what this work does.

Proposed Experiments and Decisive Checks

The first decisive check is the Dice–$\beta$ relationship. We compute it across all methods, target domains, and regions. A weak or negative rank correlation, especially in parafoveal and deep-plexus regions, would establish that Dice is an unsafe proxy for this biomarker. A strong positive correlation would falsify the premise.

The second is whether ErrorNet-style correction lowers $\beta$ relative to its own base U-Net on shifted domains, and whether dropout-aware pairs restore it. That comparison isolates the mechanism.

The third is dose-response. Measured $\hat{\Delta}$ should be roughly linear in injected $\Delta$. A flat response at small $\Delta$ would mean the pipeline cannot see disease-scale changes at all on that domain, however good its Dice.

The fourth is a sanity check against over-correction. On images with no injection, the dropout-aware model must not report spurious density loss. We check this through false-dropout rates on healthy targets.

If a labelled clinical OCTA cohort becomes available, the final check is whether the method ranking by synthetic $\beta$ matches the ranking by cross-site AD-vs-control standardized effect size. Only that result would license a claim about screening.