Many medical AI systems score how sick a patient is by measuring how far their scan departs from what healthy tissue looks like. That requires a healthy reference group, and clinical datasets often have none. The patients were recruited because they were ill, scanning healthy volunteers with CT is ethically hard, and clinical-trial cohorts exclude healthy people by design. When such a reference group does exist, it was recorded on one hospital's scanners and drawn from one population. A model calibrated against it therefore drifts when it moves to another hospital, and it cannot tell whether the drift reflects different machines or different people.
This proposal argues that disease-only cohorts already contain two kinds of control, hidden inside the patients themselves. The first is anatomy that the disease does not touch, such as air in the trachea or blood in the aorta on a chest CT. These tissues record what each scanner and protocol does to an image, and they say nothing about the disease. The second is the least-affected tissue within each patient, pooled across the cohort. It records that population's own baseline for healthy-looking tissue. We propose to use the first to remove scanner effects and the second to replace the missing healthy group. Together they would yield a severity score that needs no healthy volunteers and can be re-anchored at a new hospital without labels. As a side effect, the score splits any external performance drop into a part caused by acquisition and a part caused by population.
Core Claim
The closest existing system is cOOpD, from Prediction of disease severity in COPD: a deep learning approach for anomaly-based quantitative assessment of chest CT. cOOpD learns patch features from lung CT with self-supervised contrastive training. It then fits a density model to patches from never-smokers and scores chronic obstructive pulmonary disease (COPD) severity as how unlikely a patient's patches are under that density. It reaches 84.3% AUC on the US multi-center COPDGene test set but only 76.3% on the German COSYCONET cohort, and it depends on a curated never-smoker group that its authors call hard to assemble. Our claim has three parts, each testable on those two cohorts.
The first part is that a density fitted to the least-abnormal fraction of patches from all subjects, with never-smokers removed entirely, recovers nearly all of cOOpD's internal discrimination. The second is that conditioning the encoder's normalization statistics on disease-insensitive reference anatomy closes a meaningful share of the 8-point external gap. The third is that re-estimating the trimmed baseline from the target site's own unlabeled scans gives a local re-anchoring step that survives changes in disease prevalence.
The mechanism borrows from Stabilizing In-Context Multi-Source Domain Adaptation for Biomedical Images Through Controls. That paper conditions batch-normalization statistics on unperturbed control cells present in every microscopy plate. With this, it reaches 0.930 ± 0.019 accuracy on new batches, against 0.939 ± 0.005 in-domain, and it stays robust at batch size one and under label shift. Its method assumes that explicit negative controls are physically present. Our contribution is to show where equivalent controls hide in clinical imaging, where nobody planted them.
Research Program
The work has three components built on the cOOpD pipeline, so that every difference from it can be traced.
The first component is a reference-anatomy anchor. For each CT, we segment the trachea and main bronchi lumen and the descending aorta blood pool. Both are tissues whose intensity and texture are set mainly by the scanner, reconstruction kernel, and dose, not by lung parenchymal disease. We pass reference patches through the same encoder and use their per-scan feature statistics as the normalization context for lung patches. In effect, each scan gets its own one-sample "control well," which is the setting where the control-stabilized method held up best. We deliberately exclude skeletal muscle and subcutaneous fat. COPD causes muscle wasting and weight change, so those tissues are not disease-insensitive. We also test whether the chosen tissues are truly inert (see the decisive checks).
The second component is a trimmed normative density that replaces the never-smoker group. Let $z$ denote the anchored feature vector of a lung patch. Let $s_p(z) = -\log p(z)$ be its anomaly score under a density $p$, which is a Gaussian mixture or normalizing flow as in cOOpD. Starting from a density fitted to all patches, we iterate
$$p^{(t+1)} = \arg\max_{p} \sum_{z \in S_q^{(t)}} \log p(z), \qquad S_q^{(t)} = \{ z : s_{p^{(t)}}(z) \le \text{the } q\text{-quantile of } s_{p^{(t)}} \text{ over all patches} \},$$
so that the density is repeatedly refitted to the fraction $q$ of patches it currently finds most normal. This is the same idea as robust covariance estimation by trimming. The fixed point describes healthy-looking tissue as this population presents it. The known risk is that diffuse disease contaminates the retained set and compresses the severity scale. We will sweep $q$ and measure this compression directly against the never-smoker reference.
The third component is local re-anchoring with failure attribution. At a new site, we keep the encoder frozen and re-run the trimming step on that site's unlabeled scans. This yields a local baseline without labels and without healthy controls. It is a label-free version of the recurrent local validation advocated in All models are local: time to replace external validation with recurrent local validation, which documents the Epic Sepsis Model falling from a marketed AUC of 0.73–0.83 to 0.60–0.64 externally. Because the reference anatomy carries acquisition information only, we can split the external shift into two measurable parts. One is the distance between source and target reference-tissue feature distributions, which reflects acquisition. The other is the remaining shift in anchored lung features, which reflects population and disease mix. That split addresses the open problem that external failures cannot currently be assigned to scanners versus patients.
Population bias enters as an evaluation constraint, not as a separate fairness method. A baseline estimated from one recruitment population encodes that population's age and sex structure. We will therefore report subgroup discrimination and calibration by sex, age band, and self-reported race where the cohort records it. We will also ask whether local re-anchoring narrows or widens those gaps.
Baselines
The naive reference point is a supervised network trained on GOLD stage labels with the same encoder backbone, together with simple global intensity windowing. It shows what is achievable without any normative modeling. The keratoconus study Deep Learning Based Unsupervised and Semi-supervised Classification for Keratoconus suggests this baseline will be weaker than density-based scoring: there a supervised MLP reached 73.9% against 82.4% peak for a variational autoencoder with a mixture model.
The strongest existing method is cOOpD with its never-smoker density. It reports 84.3% AUC on the COPDGene test set and 76.3% on COSYCONET Prediction of disease severity in COPD: a deep learning approach for anomaly-based quantitative assessment of chest CT. It is the strongest competitor because it is the only method in the file that scores severity as deviation from health and has been validated across two countries. We will retrain it on our splits, with the same encoder, patch size (50×50×50 voxels), density family, and hyperparameter budget, so that its numbers are reproduced before any comparison is made.
Two adaptation competitors complete the set. The first is cOOpD followed by unanchored test-time adaptation using AdaBN and TENT on COSYCONET, which are the methods the control-stabilized paper found brittle at small batches and under label shift. The second is a "mildest patients as surrogate controls" baseline, which fits the density to GOLD 0 smokers only.
The ablations isolate each ingredient: trimming without anchoring, anchoring without trimming (never-smoker density plus reference-tissue normalization), and the full system with and without local re-anchoring. Beating cOOpD has two meanings, and both are stated in advance. Internally, the control-free full system must be within 2 AUC points of never-smoker cOOpD. Externally, it must exceed cOOpD's COSYCONET AUC with a paired bootstrap confidence interval that excludes zero difference.
Why not just…?
Why not just calibrate CT intensities to trachea air and aortic blood, then run cOOpD unchanged? This is the most serious threat, because radiologists already use such phantomless calibration. It is cheap and may capture much of the scanner effect. Our anchoring differs in that it acts on learned features and normalization statistics, so it can absorb texture and kernel effects that a linear intensity correction cannot. Whether that matters is an empirical question. The anchoring-only ablation, run against an HU-calibration baseline, settles it. If HU calibration matches feature-level anchoring on COSYCONET, we will drop the learned anchor and keep it as preprocessing. In that case the contribution narrows to trimming and attribution.
Why not just apply AdaBN or TENT at the new hospital? These methods re-estimate statistics from whatever target batch arrives, so the statistics mix scanner effects with the target's disease prevalence. Stabilizing In-Context Multi-Source Domain Adaptation for Biomedical Images Through Controls reports that this kind of adaptation degrades at batch size one and under label shift, while control-anchored statistics hold near 0.92 and 0.90 respectively. COSYCONET is a COPD cohort, so label shift relative to COPDGene is exactly the regime at issue. Our prevalence stress test runs both approaches under identical subsampled target pools.
Why not just use the mildest patients as controls? This is plausible and simple. Its weakness is that it discards most of the tissue in the cohort and still needs stage labels to choose the patients. Our trimmed estimator selects tissue rather than people, so a moderately ill patient's spared lobes still contribute to the baseline. The surrogate-control baseline is included at equal compute. If it matches trimming, we will report that the simpler rule suffices.
Why not just collect more healthy controls from more centers? For CT, the radiation-ethics constraint that cOOpD's authors note makes this slow and expensive. In addition, Fairness and Robustness of CLIP-Based Models for Chest X-Rays shows that larger pooled training data did not remove shortcut reliance or subgroup gaps. Volume alone does not address the problem our attribution step targets.
Proposed Experiments
All experiments use COPDGene (3,144 training, 786 validation, and 1,310 test subjects) and COSYCONET (446 external subjects), with the splits described in the cOOpD paper. The main outcomes are four: AUC for the COPD discrimination task as defined there; Spearman correlation of the patient score with FEV1 percent predicted and with exacerbation counts; calibration of the score against GOLD stage; and subgroup AUC and calibration gaps. Every comparison uses paired bootstrap intervals.
The first decisive check removes all never-smokers from training and compares the trimmed density to the never-smoker density on the COPDGene test set, across trimming fractions $q$ from 0.1 to 0.6. Success means the internal AUC stays within 2 points of the reproduced cOOpD. We will also plot the score distributions of the two baselines against each other to quantify severity-scale compression.
The second check is the external transfer to COSYCONET with each ablation, which states how much of the 8-point gap each ingredient closes. A pseudo-external variant holds out COPDGene centers within the US cohort, so that acquisition shift can be studied with population held roughly fixed.
The third check tests whether the reference anatomy is inert. Within a single site, a linear probe on reference-tissue features should predict scanner model and kernel well, and GOLD stage no better than chance after adjusting for those acquisition factors. If it does predict disease, the anchor is leaking biology, and we will substitute other reference structures.
The fourth check is a prevalence stress test. We subsample the COSYCONET pool used for local re-anchoring to vary the proportion of severe disease, then measure how far the local baseline and the AUC move. This is the clinical analogue of the label-shift test in the control-stabilized paper, and it is where local re-anchoring is most likely to fail.
The fifth check validates the attribution step. We compare the acquisition and population components of the measured shift with known metadata differences between the cohorts. We also report whether subgroup gaps by sex and age shrink or grow under re-anchoring. A method that improves overall AUC while widening a subgroup gap would count as a failure under this proposal.
References
- Prediction of disease severity in COPD: a deep learning approach for anomaly-based quantitative assessment of chest CT
- Stabilizing In-Context Multi-Source Domain Adaptation for Biomedical Images Through Controls
- All models are local: time to replace external validation with recurrent local validation
- Deep Learning Based Unsupervised and Semi-supervised Classification for Keratoconus
- Fairness and Robustness of CLIP-Based Models for Chest X-Rays