Auditing Opportunistic CT Screening Policies with Coverage-Certified Linear Off-Policy Evaluation

Hospitals take millions of CT scans for one reason, such as staging a cancer or checking for pneumonia. They then ignore what else the scan shows: bone density, muscle loss, visceral fat, arterial calcium. Automated tools can now read these signals reliably. What nobody can answer from existing data is the question a hospital actually faces: if we act on these incidental findings with a given rule (refer for osteoporosis workup below some bone density, within a fixed monthly referral budget), how many fractures would we prevent over the following years? A cost-effectiveness study answers a version of this question with a four-state population model. Risk models answer a different one, namely who is at risk under current practice. Neither estimates what would happen to these specific patients under a rule the hospital has never used.

We propose to treat that question as off-policy evaluation, which means estimating the long-run outcome of a decision rule using only records generated under a different rule. We use linear methods, whose error can be bounded by a computable quantity. The central observation is that the screening gap itself supplies the data needed for evaluation. In one hospital-record study, radiologists reported only about a quarter of the vertebral fractures that were visible on routine CT. As a result, patients with nearly identical CT-derived bone profiles received different downstream care. That variation in historical actions is what off-policy evaluation needs. Linear coverage theory lets us measure, before trusting any estimate, which proposed screening rules the retrospective data can and cannot evaluate.

Core Claim

Anatomical measurements extracted from routine CT form a small, interpretable feature vector: trabecular bone density, muscle area and attenuation, visceral and subcutaneous fat, and calcification. We hypothesize that this vector is close enough to "linear in its dynamics" that least-squares temporal-difference evaluation of Q-functions (LSTDQ, a method that solves a linear system to estimate a policy's long-run value from logged transitions) gives accurate value estimates for opportunistic osteoporosis-referral policies. We further claim that the feature-dynamics coverage coefficient $C^\pi_\phi$ can be computed from the same data and correctly predicts which candidate policies are evaluable. The second claim is the new part. The contribution is a certified audit of opportunistic screening policies, not a learned treatment policy, and the coverage certificate is what separates it from fitting a risk model or running deep offline RL.

Where the Pieces Come From

The motivation comes from the opportunistic screening literature. Epidemiology and reporting of osteoporotic vertebral fractures in patients with long-term hospital records based on routine clinical CT imaging found that nearly one in three elderly routine-CT patients had a vertebral fracture but only 25% of these were reported. We reinterpret that miss rate as natural variation in the behavior policy. On the predictive side, Automatic opportunistic osteoporosis screening in routine CT showed that automated trabecular density separates prevalent fractures far better than DXA (AUC 0.885 vs 0.668). Improved prediction of incident vertebral fractures using opportunistic QCT compared to DXA showed the same for incident fractures (AUC 0.76 vs 0.63). Both papers evaluate a single prediction made at one time point, not a sequence of decisions, and we keep their density thresholds as candidate policies. Comp2Comp supplies the feature extractor: an open pipeline producing spine density and muscle and fat measures with Dice scores around 0.96–0.97 at L3. It makes no decisions, and nobody has checked whether its outputs have approximately linear dynamics.

The closest decision-analytic work is Cost-effectiveness of opportunistic QCT-based osteoporosis screening. It runs a four-state Markov cohort model with population-averaged transition rates and reports that opportunistic QCT is cost-saving in women and has an ICER of $17,432 per QALY in men. It evaluates fixed strategies on a synthetic average patient. We evaluate patient-specific rules on real trajectories, and we reuse its state structure to build a ground-truth simulator.

The method comes from linear RL theory. A Unifying View of Coverage in Linear Off-policy Evaluation casts LSTDQ as an instrumental-variable problem and shows its error scales as

$$|\hat v^\pi - v^\pi| = O\!\left(\sqrt{C^\pi_\phi / n}\right),$$

where $\hat v^\pi$ is the estimated value of policy $\pi$, $v^\pi$ its true value, $n$ the number of logged transitions, and $C^\pi_\phi$ a scale-invariant coverage coefficient defined on the feature-level transition matrix. The paper requires only realizability, meaning the true Q-function is linear in the features. It is purely theoretical, assumes an invertible feature covariance, and says nothing about where the features come from. We supply real features and test whether the bound's ranking of policies holds on real data.

On Reward-Free Reinforcement Learning with Linear Function Approximation imposes a constraint on the design. Features that capture only value, and not transitions, can incur an exponential sample cost. We therefore test transition linearity directly, by checking whether next-scan features are linearly predictable from current features and action, rather than assuming it. Two papers serve as contrasts. Safe Reinforcement Learning with Linear Function Approximation needs online exploration, a known safe seed action and star-convex actions, none of which fit a retrospective, discrete refer-or-not setting, so we do not use it. Offline Guarded Safe Reinforcement Learning for Medical Treatment Optimization Strategies shows that deep offline RL on clinical records needs heavy guarding to stay near clinician behavior: unguarded variants had near-zero concordance, while their guarded method reached 0.549. It uses no imaging and has no evaluation guarantees.

Research Program

The decision problem is defined at the level of the scan. Each time a patient aged 50 or older receives a routine CT that covers the spine, the state is the Comp2Comp-plus-Bonescreen feature vector together with age, sex, prior-fracture status read from the image, elapsed time since the previous scan, and current antiresorptive therapy. The action is binary: the finding is flagged and referred for osteoporosis workup, or it is not. We read this from radiology reports and subsequent orders. Reward is minus one for each new vertebral fracture detected on the next scan, which is itself detected opportunistically by the same pipeline. A referral incurs a small cost, and a capacity penalty applies when monthly referrals exceed a budget. Scans arrive at irregular intervals, so discounting is applied per elapsed year. Patients who leave the system are treated as absorbing censoring, and this is analysed in sensitivity checks.

The work has three stages. The first is a structural test. We fit linear transition models from features and action to next features, and measure out-of-sample inherent Bellman error by regressing one-step Bellman targets for several candidate policies. We do this for three representations: interpretable anatomical features, the same features with pairwise interactions, and a 64-dimensional embedding from the segmentation backbone. This shows whether the representation that clinicians can read is also the one that supports linear evaluation.

The second stage is certified evaluation. For each candidate policy we compute $\hat v^\pi$ with ridge-regularized LSTDQ, estimate $C^\pi_\phi$ with a bootstrap interval, and report a value only where coverage passes a threshold calibrated in the simulator. The ridge term handles the invertibility problem flagged by the coverage paper.

The third stage is confounding analysis. Radiologists are more likely to report severe or visually obvious fractures. We therefore include image-derived fracture grade in the state, so that action variation conditional on the state plausibly reflects attention rather than prognosis. We then run a sensitivity analysis that bounds how much a hidden confounder of a given strength could shift each policy's estimated value. We state plainly that the instrumental-variable framing in LSTDQ addresses noise in next-state features, not confounding of actions.

The candidate policies are the ACR cutoffs of 80 and 120 mg/cm³, the Bonescreen integral cutoffs of 160 and 190 mg/cm³, a capacity-constrained rule that refers the top-k patients ranked by estimated Q-value advantage, and a rule that refers only on first detection versus one that re-flags at every scan.

Data

The file lists no public longitudinal routine-CT cohort with reports, so we must be candid about data access. The real-data arm requires an institutional long-term-records cohort of the kind used in the hospital-record epidemiology study above, restricted to patients with at least two spine-covering CTs. Comp2Comp is open and can be run locally. The ground-truth arm is semi-synthetic. We extend the Rühling Markov model so that each patient carries continuous anatomical features drawn from the real cohort's empirical distribution. Fracture hazard depends on those features in a nonlinear way, which deliberately breaks exact linearity. The behavior policy mimics a 25% reporting rate that depends on fracture grade. This gives known true values for every candidate policy and lets us check whether the coverage certificate correctly separates evaluable from non-evaluable policies.

Baselines

The naive reference is the do-nothing policy, meaning historical practice with no opportunistic action. Its value is simply the observed discounted fracture rate, and every candidate policy is reported as a difference from it.

The strongest existing decision-analytic method is the tabular Markov cohort model of Cost-effectiveness of opportunistic QCT-based osteoporosis screening. That paper reports 2.6 and 2.0 vertebral fractures prevented per 1,000 women and men over five years, and an ICER of $17,432 per QALY in men. We re-estimate its transition rates from our own cohort, so that it uses the same data, and compare its policy values to ours on the simulator's true values. Beating it means lower absolute value error on the simulator and, on real data, policy rankings that survive the confounding sensitivity analysis where the Markov model's rankings do not.

The strongest statistical competitor is a Cox proportional-hazards model on the same features, combined with a model of how referral changes the hazard to produce counterfactual fracture rates. A doubly robust estimator also belongs in this tier. It combines inverse propensity weighting on reporting with a fitted outcome model. The deep competitor is fitted Q evaluation with a two-layer network, which also gives a coverage-free estimate. All estimators receive the same training split, the same features, and the same hyperparameter search budget of 50 configurations selected on held-out Bellman error. For OPE accuracy on opportunistic screening data there is no reported result found on Lacuna. On the simulator, the comparison is therefore on absolute value error and on how often each method's 90% interval contains the true value.

Two ablations isolate the key ingredients. In the first, we remove the CT features and keep only age, sex and prior fracture. This tests whether the opportunistic measurements matter for value estimation and not just for prediction. In the second, we report LSTDQ values without the coverage gate, to show what the certificate prevents.

Why not just…?

Why not just use a static density threshold, which already reaches 84% sensitivity and 78% specificity? The threshold is not a competitor to the method. It is one of the policies being evaluated. Those sensitivity and specificity figures (Automatic opportunistic osteoporosis screening in routine CT) describe how well density detects fractures that already exist. They say nothing about how many future fractures acting on the threshold would prevent, or whether a lower cutoff under a referral cap would prevent more. If the audit concludes that a simple threshold is near-optimal among evaluable policies, that is a useful finding in its own right.

Why not just fit a Cox model and refer the highest-risk patients? This is the real threat. If referral has a roughly uniform effect and re-scanning adds little information, then ranking patients by risk is essentially what a capacity-constrained value rule does. We include it as a full baseline. The simulator lets us vary how heterogeneous the treatment effect is and whether repeated scans carry information. If the Cox ranking matches LSTDQ under realistic settings, we will say so and present the coverage certificate as the remaining contribution, since it tells the hospital which rankings can be trusted. The Cox model alone gives no such guarantee.

Why not just use deep offline RL or deep fitted Q evaluation? Deep methods give no coverage diagnostic, which is the point of this audit. Offline Guarded Safe Reinforcement Learning for Medical Treatment Optimization Strategies found that unguarded deep clinical RL collapsed to near-zero concordance with clinician behavior. Our head-to-head comparison with deep fitted Q evaluation on simulator error and interval coverage settles the accuracy question directly. With a state of about ten dimensions and a binary action, we expect little gain from the extra capacity.

Why not just extend the tabular Markov model? Discretizing six or more continuous biomarkers makes the number of states grow exponentially. The Markov model's fixed transition rates also cannot represent how a patient's own density trajectory changes their next transition. The Markov baseline arm tests this directly.

Decisive Checks

Four results would decide the proposal. The first concerns structure. If out-of-sample inherent Bellman error on anatomical features is not clearly lower than for the age-and-sex-only features, the linear premise fails and we report a negative result. The second concerns calibration. On the simulator, the estimated $C^\pi_\phi$ should rank policies by their true LSTDQ error, with a Spearman correlation we target above 0.7, and the coverage gate should reject the policies whose estimates are badly wrong. The third concerns the scaling law. LSTDQ error on the simulator should fall roughly as $1/\sqrt{n}$ as cohort size grows, which is the rate given by the coverage bound. The fourth concerns robustness. On real data, the ordering between the ACR rule, the Bonescreen rule and the capacity-constrained rule should survive the confounding sensitivity analysis at plausible confounder strengths. If the ordering flips, the honest conclusion is that retrospective data cannot settle the choice, and a prospective randomized rollout of flagging is needed.