Is Deep-Learned Retinal Fractal Dimension a Biomarker or a Camera Fingerprint?

Fractal dimension measures how densely a branching structure fills space as you zoom in. Computed on the blood vessels visible in a photograph of the back of the eye, it is one of the cheapest candidate early warning signs of Alzheimer's-type decline. The retina's smallest vessels thin out in mild cognitive impairment before brain scans show visible shrinkage. The catch is access. The standard pipeline first traces every vessel into a black-and-white map and then counts boxes on that map. It fails on blurry or dim photographs, and it discards 26% to 43% of UK Biobank images. A recent deep network, DART, skips the tracing step and predicts fractal dimension directly from raw, degraded photographs. That recovers most of those images at over a thousand images per second.

The field has not asked whether the number DART outputs is still a measurement of vessels. Deep networks trained on UK Biobank retinal photographs are already known to pick up which assessment center took the picture, even though every center used identical cameras. The images DART rescues are also not a random sample. They are disproportionately the blurry ones, which likely come from older participants and eyes with media opacities. This note proposes to audit deep fractal estimates for acquisition confounding. It then asks whether the confounding can be removed without also removing the age- and disease-related signal that makes the biomarker worth having. Finally it tests whether the "rescued" images carry the same association with cognitive outcomes as the images the old pipeline kept.

Core Claim

The claim has two parts, both testable. First, a network trained to reproduce fractal dimension under synthetic degradation will make errors that depend on image quality and acquisition center in a nonlinear way that shifts with the true value. Adding center and quality as regression covariates downstream cannot fully remove such errors. Second, the error can be constrained during training by penalizing any dependence of the estimation error on acquisition variables only, without touching biological covariates. If so, the full image set becomes usable for confounder-adjusted association studies. The alternative is that complete-case analysis on "good" images is quietly biased by who gets good images.

What is new is where the confounder control sits. It applies to an interpretable intermediate measurement, and it separates two kinds of covariate. Nuisance variables (center, illumination, blur) should be removed from the measurement itself. Biological variables (age, blood pressure, axial length) should be adjusted for only at the analysis stage, because removing them from the measurement would erase true signal.

How the directions fit together

The directions do not get equal weight. Fractal dimension analysis supplies the measurement and diagnostic accessibility supplies the application. Confounder control is the method and the main contribution.

Four papers motivate the work. Retinal microvasculature dysfunction is associated with Alzheimer's disease and mild cognitive impairment studied a 90-person memory clinic cohort with OCT angiography, a scan that images blood flow in the retinal layers. It found that fractal dimension of the superficial capillary layer separated MCI/AD from controls with AUC 0.77, against 0.56 for an MRI atrophy score. The review Retinal imaging in Alzheimer's disease reports odds ratios of 1.35 to 1.47 per standard-deviation decrease in fundus arteriolar and venular fractal dimension. It explicitly warns that these metrics are confounded by age, axial length and systemic disease. The meta-analysis A Systematic Review and Meta-Analysis of Retinal Microvascular Features in Alzheimer's Disease confirms vessel density loss across 859 eyes but does not pool fractal indices. None of these works at population scale on cheap fundus photographs, and none checks whether the measurement pipeline itself is biased.

Two papers supply the method and the threat. Robust and efficient computation of retinal fractal dimension through deep approximation trains a ResNet-18 on fundus images with synthetic blur, noise and occlusion to reproduce VAMPIRE-pipeline fractal labels. It reaches $r = 0.9572$ on clean test images and $r = 0.8817$ under the most severe degradation. It was never audited for center or demographic effects and never tested against a clinical outcome. We reuse its training recipe as the starting point. On Biases in a UK Biobank-based Retinal Image Classification Model trained InceptionV3 end to end to predict hypertension, with overall AUC 71%. It found a 10% AUC gap between centers with identical hardware and a 15% gap across age groups. Most mitigation methods it tried, including GroupDRO and domain-independent training, closed gaps by "leveling down" overall performance, and SWAD did not close the age gap. That negative result constrains our design. We do not debias a disease classifier. We debias a scalar measurement against nuisance variables only, where leveling down on biology is not the goal.

Secondary porosity generation plays a deliberately small role. Its value here is as a cautionary precedent for measurement confounding, not as an analogy. In Fractal Characterization of Nanopore Structure in Shale, Tight Sandstone and Mudstone from the Ordos Basin of China Using Nitrogen Adsorption, a fractal model is fitted to gas-uptake curves from rock samples. It produced a surface dimension as low as 1.1755, below the physical floor of 2 for a surface. That is a clear sign the estimator was absorbing experimental artifacts rather than pore geometry. We borrow one concrete tool from this: a physical-plausibility check. Retinal vessel fractal estimates outside the range the reference pipeline ever produces, or behaving implausibly across a person's two eyes, are flagged as estimator failures rather than biology. We do not pursue the proposed link between rock cementation and vascular pruning. That would be a metaphor with no measurable consequence here.

Research Program

The work proceeds in three stages on UK Biobank fundus photographs. We use the same image pool and VAMPIRE-derived labels that DART used.

The first stage is an audit. Let $D_{ref}$ be the VAMPIRE fractal dimension on an image the standard pipeline accepts. Let $\hat D$ be the network's prediction and $e = \hat D - D_{ref}$ its error. On gradable images, and on the same images with DART-style synthetic degradation applied at known severity, we test two things. One is whether assessment center, an automated quality score and illumination statistics predict $e$ beyond $D_{ref}$. The other is whether that dependence is merely an additive shift or interacts with $D_{ref}$ and degradation severity. The interaction is what matters. A severity-dependent shrinkage toward the mean compresses exactly the low-fractal eyes that screening cares about. Covariate adjustment at the analysis stage cannot undo that.

The second stage is nuisance-invariant training. We train the estimator with

$$\mathcal{L} = \mathbb{E}\big[(\hat D - D_{ref})^2\big] + \lambda\,\mathrm{Dep}\big(e,\; A \mid D_{ref}\big),$$

where $A$ collects acquisition variables only (center, quality score, degradation severity). $\mathrm{Dep}$ is a measure of statistical dependence conditioned on the true value, implemented as an adversary that tries to predict $A$ from $e$ and $D_{ref}$. $\lambda$ trades accuracy for invariance. Age, blood pressure and refractive error are deliberately excluded from $A$, because they plausibly cause real changes in vessel geometry. Removing them from the measurement would be the over-adjustment the confounding literature warns about.

The third stage is outcome validation with selection made explicit. Using the resulting fractal estimate on all images, including those the standard pipeline rejects, we fit the same multivariable model for each estimator. The model regresses cognitive test performance, and incident cognitive decline where follow-up exists, on fractal dimension. It adjusts for age, sex, blood pressure, diabetes, refractive error and center. We then compare the association in the previously-accepted and previously-rejected strata.

Baselines

The naive reference is the status quo: VAMPIRE fractal dimension on images the pipeline accepts, with rejected images simply dropped. It defines the association we are trying to preserve and the population coverage we are trying to extend. It "wins" if rescued images add noise or bias that outweighs their added sample size.

The strongest existing method is DART (Robust and efficient computation of retinal fractal dimension through deep approximation). It reports Pearson $r = 0.9572$ and $R^2 = 0.9160$ on 14,907 clean test images, and $r = 0.8817$ under severity-5 degradation. We retrain it on our split with its published architecture, augmentation and tuning budget, matched in epochs and hyperparameter trials to our model. We do not report a DART number for any cognitive or dementia outcome, because no reported result was found on Lacuna for DART fractal dimension against cognitive outcomes. We beat DART only if three conditions hold together. Our clean-image correlation must stay within 0.01 of its $r$. Center and quality must become non-predictive of $e$ given $D_{ref}$. And the downstream fractal–cognition association must be more stable across quality strata.

The simple competitor is DART followed by linear residualization of $\hat D$ on center and quality score before the association model. This is the textbook partialling-out approach, it costs nothing, and it is the baseline most likely to match us. The key ablation drops the conditioning on $D_{ref}$ from the invariance penalty, making the error independent of $A$ unconditionally. This isolates whether conditioning on the true value is what prevents erasing real between-person variation. A second ablation adds age to $A$, to show directly what over-adjusting a biological variable does to the outcome association.

Why not just…?

Why not just residualize DART's output on center and image quality afterwards? This is the real threat, and it may work. If the audit in stage one finds that errors are an additive shift by center and quality, residualization is exactly correct and our training penalty is unnecessary. We would report that as the finding. Residualization fails only if error depends on the true fractal value, for example through heavier shrinkage in low-quality images. It cannot restore compressed variance. The stage-one interaction test settles which world we are in before any new model is trained.

Why not just train an end-to-end classifier from fundus photographs to cognitive impairment? The file's evidence is that end-to-end retinal models absorb site and age structure. On Biases in a UK Biobank-based Retinal Image Classification Model found a 10% AUC center gap and a 15% age gap, and the fixes mostly leveled down. An end-to-end dementia classifier would also give up the property that makes fractal dimension auditable: a scalar with an external reference and known biological covariates. We include such a classifier only as a secondary comparison of predictive AUC. We do not treat it as a replacement.

Why not just keep excluding low-quality images, as current pipelines do? Exclusion is a selection step, and image quality plausibly tracks age and eye disease. Complete-case estimates may therefore describe a healthier population than the one screening targets. Stage three tests this directly. If rejected-stratum associations match accepted-stratum ones after adjustment, exclusion only costs power. If they differ, exclusion was biasing published effect sizes.

Why not just use vessel density or caliber, which need no fractal machinery? In the memory clinic cohort, capillary fractal dimension changed in MCI where larger-vessel measures did not (Retinal microvasculature dysfunction is associated with Alzheimer's disease and mild cognitive impairment). That makes fractal dimension the more interesting target. Our pipeline can nonetheless be applied to caliber as well, and we report it as a comparator in the outcome models.

Decisive Experiments

The first check is the audit itself. In a held-out test set, we predict center and quality from DART's error with and without $D_{ref}$ and severity interactions. If the interaction terms add no predictive power, the proposal reduces to recommending residualization, and we publish that. The second check is invariance without accuracy loss. For our model against retrained DART, we compare center-classification accuracy from $e$ against chance and Pearson $r$ with $D_{ref}$ on clean and severity-5 images. Left–right eye agreement serves as a label-free consistency test on images that have no reference label. The third check is the plausibility screen borrowed from the rock-physics lesson: the fraction of predictions outside the reference pipeline's observed range, stratified by quality. The fourth check is the outcome test. For each estimator we compute the adjusted fractal–cognition coefficient in accepted versus rescued images, along with its confidence interval. We also run the age-in-$A$ ablation, which should visibly weaken the association and demonstrate the over-adjustment cost. The proposal succeeds if the nuisance-invariant estimate yields rescued-stratum associations consistent with accepted-stratum ones, while plain DART and residualized DART do not.