When to Treat Bone Loss Seen on Routine CT: Treatment Thresholds, Not Risk Thresholds

Millions of patients, especially those with cancer, get abdominal CT scans every few months for reasons unrelated to their bones or muscles. Software can already read these scans automatically. It finds each vertebra, measures how dense the spongy bone inside it is, and measures how much muscle and fat sit at the lower spine. A repeat scan therefore traces how a patient's skeleton and muscle change over time, at no extra cost. Today almost nobody uses that trajectory to decide when to start bone-protective drugs. This proposal asks a narrow, answerable question. Given serial routine CT scans, what simple rule of the form "start an antiresorptive drug once vertebral bone density falls below c, or falls faster than d per year" prevents the most new vertebral fractures? Does adding muscle density to the rule help?

The idea behind the question is easy to overlook. Clinical epidemiology is full of studies that fit a smooth curve to risk and report a "tipping point" where risk starts climbing. It is tempting to read that point as the place to intervene. It is not. Where risk rises tells you who will get hurt. Where treatment helps most tells you whom to treat, and the two points need not coincide. We propose to estimate the treatment threshold directly, as the parameter of a small family of dynamic treatment rules, from longitudinal CT measurements whose noise we model explicitly. We then test whether it differs from the risk tipping point that the standard spline analysis would have recommended.

Core Claim

A dynamic treatment regime is a rule that maps a patient's evolving measurements to an action at each visit. We claim three things about such rules. First, a low-dimensional threshold regime, indexed by one or two cutoffs on CT-derived vertebral density and muscle density, can be estimated reliably from the few thousand longitudinal patients a single health system can supply. Second, the estimated optimal cutoff will generally differ from the inflection point of a restricted cubic spline risk curve fitted to the same data. A restricted cubic spline is a flexible piecewise-polynomial curve, the workhorse of the non-linear risk literature. Third, ignoring scan-to-scan measurement error biases both the risk inflection point and the regime threshold in predictable directions, and a simple latent-state smoother removes most of that bias.

The formal object is small. Let $M_t$ be the patient's true trabecular density at scan $t$, observed with noise as $\tilde M_t$. Let $g_c$ be the rule "start therapy at the first scan where the smoothed estimate of $M_t$ falls below $c$." Let $Y^{g_c}$ be the fracture-free outcome we would see if everyone followed $g_c$. We estimate

$$c^\ast = \arg\max_c \; \mathbb{E}\big[Y^{g_c}\big] - \lambda\, \mathbb{E}\big[\text{treated-time under } g_c\big],$$

where $\lambda$ prices drug exposure and harms. The contrast we care about is between $c^\ast$ and the risk inflection point $c_r$ of the untreated hazard curve $h_0(m)$. The two coincide only if the treatment benefit $\tau(m) = h_0(m) - h_1(m)$ crosses $\lambda$ exactly where $h_0$ bends. That is a strong assumption, and nothing in the existing literature checks it.

Why This Gap, and Why This Framing

The four directions supply different pieces, and they do not carry equal weight here.

Automated vertebral segmentation supplies the measurement, and its known error budget constrains the design. Comp2Comp is an open-source pipeline. It uses a pretrained TotalSegmentator model to segment T12–L5, places a region of interest in each vertebral body to read bone density in Hounsfield units, and segments muscle, visceral fat and subcutaneous fat at L3. It reports region-of-interest mean errors below 7.10 HU. The SpineQ cadaver study extracts phantom-free volumetric bone mineral density across 14 scanner protocols. It finds an intraclass correlation of 0.992 with quantitative CT but an RMSE of 12.65 mg/cm³, which falls to 8.93 mg/cm³ once a degenerated vertebra is excluded. These numbers say that agreement on a single scan is excellent. They also say that the noise in a difference between two scans can be as large as a year's true bone loss. Both tools are cross-sectional extractors. We reuse them as the observation model and do not modify them.

Body composition granularity supplies the reason to look past bone alone. In the Dutch melanoma immunotherapy cohort, 1,471 patients were measured by automated CT segmentation. Skeletal muscle density (HR 0.88 per SD) and visceral fat index (HR 1.12 per SD) predicted survival, while BMI had no association. That study motivates including muscle radiodensity, which no surface or anthropometric proxy can see. It used linear Cox models and a single static treatment choice. We carry its tissue measures into a sequential, non-linear setting.

Non-linear risk modeling supplies the comparison point and a warning. Studies such as the ECW/TBW mortality cohort report a flat risk below 42.4% and a rising risk above it. The NPAR cardiovascular study puts its threshold at 14.21. The MIMIC-IV intra-abdominal pressure study puts its threshold at 16 mmHg. All of these are inflection points of risk at one time point, fitted without external validation. We treat this way of finding thresholds as the main thing to beat, not as something we inherit.

Dynamic treatment regimes supply the estimation machinery, and they impose the hardest constraint. EpiCare shows that offline reinforcement learning needs about 2,000 patient episodes to beat standard care, falls below random under 256 patients, and that direct-method off-policy evaluation reached an RMSE of 106.4 on a 100-point return scale. The critical reexamination of RL for treatment regimes ran 17,550 evaluation experiments on MIMIC-III sepsis. It found that random policies often "win" under standard off-policy evaluation and that results swing with reward design. Both papers push us away from a deep RL policy over imaging states and toward a regime class with one or two parameters. Estimating such a class is closer in spirit to the recurrent g-computation of G-Net than to Q-learning, and its variance is far smaller.

Finally, Aali et al. found that AI read sarcopenia from CT in many patients whose charts carried the diagnosis code only 0.5% of the time. That finding cuts two ways. It suggests clinicians are largely not acting on opportunistic CT signals, so the logged behavior policy probably ignores the very signal we study, and there is room to improve on it. It also means codes cannot define either our states or our outcomes. We therefore define the action from prescription records and the outcome, new vertebral compression fracture, from vertebral height loss segmented on the next CT. That keeps both ends of the loop inside the imaging.

Research Program

The first component is a longitudinal observation model. We run Comp2Comp on every abdominal CT for each patient. We extract L1–L3 trabecular density, L3 muscle density and area, and visceral fat area, along with contrast phase, tube voltage and slice thickness. A linear-Gaussian state-space model, essentially a Kalman smoother, then treats each patient's true density as a slowly drifting latent variable. Its observation noise variance is set by protocol, with a prior anchored to the SpineQ and Comp2Comp error figures and refined on same-day or within-week repeat scans. Contrast phase gets an explicit offset term, because a contrast-enhanced scan followed by a plain one produces apparent density changes that are not biological. Vertebrae flagged for cement, severe osteophytes or existing fracture are excluded from the state, since segmentation is known to degrade there.

The second component is regime estimation. We define threshold regimes on the smoothed density, on its smoothed slope, and on the two-dimensional pair of density and muscle density. We estimate the value of each candidate threshold with a doubly robust g-formula: a model of who gets prescribed antiresorptives, combined with a model of fracture-free time given history. We then pick $c^\ast$ by maximizing over a grid, with cross-fitting and a bootstrap confidence interval on $c^\ast$ itself. We separately fit the spline risk curve on untreated person-time and locate $c_r$ by the usual piecewise search.

The third component is a semi-synthetic testbed, since off-policy evaluation on real data cannot be trusted on its own. We keep real patients' covariate and scan trajectories, including real noise and real gaps between scans. We then simulate treatment assignment and fractures from known mechanisms in which we control $h_0$, $\tau$, and the gap between $c_r$ and $c^\ast$. This gives ground-truth regime values against which every estimator, ours and the baselines', can be scored. That evaluation method follows the lesson of EpiCare, but on realistic imaging states rather than abstract symptoms.

The data source must be a health-system archive of serial abdominal CT linked to prescriptions, of the kind Aali et al. drew on at Stanford. Oncology patients under routine restaging are the natural population, because they are scanned every few months and many receive glucocorticoids or hormone therapy that accelerate bone loss. No dataset in the research file supplies this longitudinal linkage. Assembling it is part of the work.

Baselines

The naive reference point is the logged standard of care, meaning what clinicians actually did, evaluated by its observed fracture-free time. Alongside it we evaluate "never treat on CT grounds," estimated with the same g-formula so the comparison is on equal footing. Beating the logged policy means a significantly higher estimated fracture-free time at equal or lower treated-time, with a bootstrap interval that excludes zero.

The strongest conceptual competitor is the risk-threshold regime: treat once smoothed density crosses the spline inflection point $c_r$. This is what a clinician would derive from the non-linear risk literature. It gets exactly the same states, smoother and outcome model, so the only difference is how the threshold is chosen. Beating it in the semi-synthetic testbed means higher true value whenever $c_r \ne c^\ast$ by design, and no loss when they coincide. In real data, beating it means the estimated value difference is significant and $c^\ast$ falls outside the confidence interval of $c_r$.

The strongest existing algorithmic method is offline RL, specifically conservative Q-learning, which EpiCare found to be the best-performing family. We give it the same smoothed state vector, the same reward of fracture-free time minus $\lambda$ times treated-time, and a matched tuning budget measured in configurations tried and selected by the same held-out criterion. No reported result found on Lacuna for offline RL on CT-derived body composition states. The reference figures we hold it against are EpiCare's: roughly 2,000 episodes needed to beat standard care, performance below random under 256 patients, and a direct-method evaluation RMSE of 106.4 on a 100-point scale. In the semi-synthetic testbed we will plot true value against cohort size for both CQL and the threshold regime, so the crossover point, if one exists, is measured rather than assumed.

Behavior cloning, a supervised model that imitates clinicians' prescribing from the same states, is the competitor the sepsis reexamination found hardest to beat. We run it with the same features and use it both as a policy and as the propensity model.

Three ablations isolate the proposal's ingredients. The first removes the measurement-error smoother and thresholds raw per-scan values. The second removes muscle density and uses bone density alone. The third replaces CT states with BMI and waist-based indices such as the weight-adjusted waist index, to test whether CT granularity matters at all.

Why not just…?

Why not just run offline RL on the imaging states? Because the available evidence says it will lose at the cohort sizes a single institution can supply, and that we could not tell even if it won. EpiCare puts the crossover at about 2,000 episodes and documents an off-policy evaluator whose error exceeded the whole reward scale. The sepsis reexamination shows random policies often looking best under standard evaluation. A one- or two-parameter regime cuts estimation variance drastically, and the clinical decision really is a single start/no-start choice. We still run CQL, and the sample-size curve in the semi-synthetic testbed will show whether that caution is warranted.

Why not just fit a Cox model with time-varying density and treat whoever is at high predicted risk? This is the most serious alternative, and it is exactly the risk-threshold baseline. If treatment benefit happens to be largest where untreated risk is highest, it will match us, and the experiments will say so honestly. Two things argue against assuming that. First, the drug's effect can saturate at very low density, where the bone architecture is already lost, which would put $c^\ast$ above $c_r$. Second, a Cox model of risk conditions on past treatment, which is both caused by earlier density and affects later density. This is the time-varying confounding problem that motivates g-methods in the first place. The semi-synthetic testbed is built to show when each failure appears.

Why not just use BMI, anthropometric indices, or surface geometry and skip segmentation? AbdCTBench shows that external abdominal shape predicts mortality with AUROC 0.839 and aortic calcium with AUROC 0.848. That is a strong showing for cheap proxies. But surface shape cannot measure trabecular bone density or muscle radiodensity, and in the melanoma cohort BMI carried no survival signal while muscle density did. The BMI and weight-adjusted-waist ablation tests this directly for the fracture outcome. If it matches the CT regime, the conclusion is that segmentation is unnecessary here, and we will report that.

Why not just imitate clinicians? Clinicians acting on information the model cannot see, such as dual-energy X-ray results, is a real threat to any claim of improvement, so we include those results where recorded and run an unmeasured-confounding sensitivity analysis. But the coding gap Aali et al. document suggests opportunistic CT findings rarely reach decisions at all. Imitation would therefore reproduce a policy that largely ignores the signal. Behavior cloning is run as a baseline, so this argument is tested rather than asserted.

Proposed Experiments and Decisive Checks

The first experiment validates the observation model. On patients with repeat scans within a short interval, we measure how much apparent density change comes from noise, with and without the smoother and the contrast-phase term. We expect raw scan-to-scan differences to have a spread comparable to the 7–13 HU or mg/cm³ error figures above, and the smoother to shrink it substantially. If it does not, slope-based rules are not viable and we restrict to level-based thresholds.

The second experiment is the semi-synthetic test of the core claim. We vary the true gap between $c_r$ and $c^\ast$, the cohort size from 250 to 5,000 patients, and the noise level. For each estimator we score regret against the known optimal regime and the coverage of its confidence interval for $c^\ast$. The decisive outcome has two parts: the threshold-regime estimator should beat the risk-threshold rule whenever the gap is non-zero, and it should beat CQL below roughly the EpiCare crossover. If the risk-threshold rule is never meaningfully worse, the central claim fails.

The third experiment runs on the real archive. We report $c^\ast$ and $c_r$ with their intervals, the estimated value of each regime, and the ablations. Two negative-control checks guard the result. Regime "value" estimated for a drug with no plausible bone effect should be null. The ranking of regimes should be stable across the 13-patient-group style stratification that the sepsis reexamination showed can flip RL conclusions. The headline finding would be a credible, measurable separation between where fracture risk bends and where treatment should start, estimated from scans that patients have already had.