After spinal fusion surgery, a spacer called a cage is placed between two vertebrae. If the cage is much stiffer than the bone around it, it carries most of the load. The bone, no longer stressed, thins out, a process called stress shielding, and the cage can sink into the vertebra, which is called subsidence. A tool that could say "this patient is very unlikely to subside, skip the extra CT and the clinic visit" would be useful. Its safety would be measured by negative predictive value (NPV), the fraction of patients it clears who truly have no event.
There is a basic problem with any such tool built from hospital archives. Follow-up CT scans after fusion are mostly ordered for patients who have pain or worrying X-rays. The outcome label therefore exists mainly for a selected group, and the NPV measured on that group may not match the NPV at deployment. The error could go either way. Hospitals also differ in how often they re-image, how common subsidence is, and which scanners they use.
This note proposes to replace the usual single NPV number with a lower bound that stays valid when the choice of who got re-imaged depends on things the records do not capture. The tool then clears only as many patients as that bound allows. The claim that can actually be tested is this: the strength of selective re-imaging can be measured at hospitals that re-image every patient by protocol. That measured strength can then be carried to hospitals that re-image only symptomatic patients. The resulting bounds should hold at those hospitals, while naive and standard-corrected NPV estimates do not.
Core Claim
A rule-out model has two jobs: rank patients by risk, and certify an operating threshold. Most work on high-NPV triage concentrates on the ranking. Examples are the gradient-boosting bleeding model that reached 98% NPV on an external cohort (Prediction of Outcome in Acute Lower Gastrointestinal Bleeding Using Gradient Boosting) and the bone-metastasis system that cleared 64.7% of 54,610 consecutive CT patients at 98.2% NPV (A clinically applicable AI system for detection and diagnosis of bone metastases using CT scans). Both report the certified NPV as if the labeled patients stood in for everyone.
Other papers name the selection problem but do not correct it. The prostate study reached 100% NPV only among men selected for systematic biopsy despite a negative MRI (Analysis of risk factors for determining the need for prostate biopsy in patients with negative MRI). The airway radiomics paper notes that requiring a repeat test one year later conditions the cohort on a particular clinical path (A novel computed tomography radiomic nomogram for early evaluation of small airway dysfunction development). The vertebral fracture dataset notes that patients are filtered by being sick enough to receive CT (A Vertebral Segmentation Dataset with Fracture Grading).
We treat the operating threshold as the object to certify. Take the patients a model clears at threshold $t$. Let $\pi$ be the fraction of them who received follow-up CT, and $p$ an upper confidence bound on the event rate among those verified. Suppose that, given the recorded variables, the odds of being re-imaged differ between patients with and without subsidence by at most a factor $\Gamma \ge 1$. This is a sensitivity parameter in the style of observational-study sensitivity analysis. The worst-case event rate among unverified cleared patients is then $q_\Gamma = \Gamma p / (1 - p + \Gamma p)$, and
$$\text{NPV}_{\text{lb}}(t) = 1 - \big[\pi\, p + (1-\pi)\, q_\Gamma\big].$$
The deployed threshold is the one that clears the most patients subject to $\text{NPV}_{\text{lb}}(t) \ge 0.98$. At $\Gamma = 1$ this reduces to the standard missing-at-random correction. The new ingredient is estimating $\Gamma$ empirically from hospitals with protocol follow-up, and testing whether it transfers, rather than choosing it by hand. The same machinery also absorbs performative effects. A surgeon who sees early lucency and restricts weight-bearing turns a would-be event into a recorded non-event. Evaluating and Correcting Performative Effects of Decision Support Systems via Causal Domain Shift formalizes this, and we fold it into $\Gamma$ as an unrecorded intervention.
Stress shielding enters as the application and as a candidate feature, not as the main claim. The two finite element studies in the file disagree about which cage material raises endplate risk. Porous titanium improved stability by 15% over PEEK, a polymer cage, in Biomechanical Comparison of Two Intervertebral Fusions for L4-L5 Spinal Segment Using the Finite Element Methods. A titanium frame with a PEEK core cut L4 endplate peak stress by 54.2% relative to pure titanium in Biomechanical design of titanium-PEEK combined fusion cage based on PLIF surgical model. Both rest on single idealized geometries. We compute a cheap patient-specific load-sharing index and ask whether it earns a place in a certified rule-out model. The index uses the parallel-spring ratio of cage stiffness to endplate bone stiffness, with bone modulus estimated from CT-derived density.
Research Program
The work has three parts.
The first part builds the per-patient inputs from the immediate postoperative CT. A vertebra segmentation and labeling model is trained on VerSe. It locates the cage and the adjacent endplates. Endplate density is estimated in the way the opportunistic density measurements of A Vertebral Segmentation Dataset with Fracture Grading were made. That dataset also annotates foreign bodies, which makes it the natural public set for developing cage localization. Density is mapped to a modulus, and together with the cage material and footprint this gives the load-sharing index.
The second part is the certification procedure above. $\Gamma$ is estimated at protocol-follow-up hospitals by comparing each site's complete-verification NPV with what its symptom-driven subset alone would have suggested.
The third part tests heterogeneity directly, leaving out one hospital at a time. VerSe shows that scanner vendor and anatomical variants such as L6 vertebrae produce "one-label shift" errors. A shifted label would attach the density estimate to the wrong endplate. We therefore report certification failures separately for patients with transitional anatomy, as a subgroup check on hidden false negatives.
The clinical data do not exist publicly. We would assemble a retrospective multi-center fusion cohort. Its essential design requirement is that at least two hospitals obtain routine CT at about 12 months for every patient, and that several hospitals re-image only on clinical indication.
Baselines
The naive reference fits a gradient-boosting classifier to verified patients only. This is the same model family that gave the 98% external NPV in the bleeding study (Prediction of Outcome in Acute Lower Gastrointestinal Bleeding Using Gradient Boosting). Its threshold is set for 98% NPV on pooled verified patients. It shows what current practice would certify.
The strongest existing competitor combines three ingredients: inverse-probability weighting of verified patients by their modeled probability of being re-imaged, per-site recalibration of the threshold on each hospital's verified patients, and the repeated-regression correction of Perdomo et al. for performative label changes. It is the strongest competitor because it already handles every bias we name, except selection on unrecorded factors. For the image features, the strongest applicable detector is an in-house convolutional network of the kind Riedel et al. benchmarked. Their in-house models reached vertebral-level AUROC 0.923, against 0.964 for the commercial SpineQ, on the VerSe test set. SpineQ cannot be retrained, so the in-house architecture is the fair comparator.
All methods receive the same patients, features, hyperparameter search budget, and leave-one-hospital-out splits. The weighting model is given every recorded variable our method sees. For subsidence rule-out itself, no reported result was found on Lacuna. The nearest reference points are the 98.2% NPV at 64.7% cleared from the bone-metastasis system and the 98% external NPV from the bleeding model.
Our method beats the competitor under either of two outcomes. In the first, its certified bound covers the true NPV at the protocol-follow-up test hospitals while the competitor's estimate overshoots. In the second, coverage is equal and our method clears at least as many patients.
Two ablations isolate the key ingredients. The first sets $\Gamma = 1$, which is exactly the weighting baseline and removes the transferred sensitivity parameter. The second removes the load-sharing index and replaces it with raw endplate Hounsfield units, the CT density scale. On a subset of about 30 patients per material, we also run full patient-specific finite element models in the style of Li and Liu. This checks whether the cheap index tracks simulated endplate stress.
Why not just…?
Why not just recalibrate the threshold at each hospital on its own labeled follow-ups? Those labels are the selected ones. Recalibrating on them reproduces whatever bias the hospital's re-imaging habits introduce, however many labels there are. The leave-one-hospital-out comparison against the per-site recalibrated baseline measures this directly at the protocol-follow-up hospitals, where the true NPV is known.
Why not just use standard verification-bias correction, weighting verified patients by their probability of being re-imaged? This is the real threat. If re-imaging depends only on recorded variables such as pain scores, X-ray lucency notes, and clinic visits, weighting is enough and $\Gamma$ will be estimated near 1. If the protocol hospitals show that the weighted estimate already covers the true NPV, we will report that and drop the bounded-selection machinery. The contribution would then shrink to the heterogeneity analysis and the multi-center benchmark. Yang and Perdomo et al. give reasons to expect unrecorded drivers of re-imaging, but that remains an expectation, not evidence for this setting.
Why not just rule out on endplate bone density alone, skipping machine learning and mechanics? A single density threshold could plausibly match a learned model. The file shows single markers underperforming combinations: PSA alone had AUC 0.6607 against 0.8478 for PSA density in the prostate cohort. That result is in another disease, however. The Hounsfield-unit ablation is run through the same certification procedure. If it clears as many patients at the same certified NPV, the load-sharing index is unnecessary and we say so.
Why not just run full finite element models for every patient? They take hours per patient and still assume idealized bone properties. The Li and Liu disagreement shows these assumptions can flip conclusions. The finite element subset tells us whether the cheap index agrees with full simulations well enough to substitute for them.
Proposed Experiments
The first experiment is a public, semi-synthetic check on VerSe fracture rule-out, done before any clinical data are collected. We hide labels for vertebrae according to a known selection rule. The rule depends on fracture grade and on a hidden variable that stands in for unrecorded symptoms. We then hold out one scanner vendor at a time. Because ground truth is complete, we can measure how often each method's certified NPV bound is at or below the true NPV (coverage), and the fraction of vertebrae cleared, across a sweep of hidden selection strength. The pass condition is that coverage stays at the nominal level when $\Gamma$ is estimated from held-out "protocol" vendors. The weighting baseline should fail once the hidden variable matters.
The decisive clinical experiment certifies thresholds using only symptom-driven hospitals, with $\Gamma$ taken from one protocol hospital. The certified threshold is then applied to the second protocol hospital, where every patient was re-imaged. The primary outcome is whether true NPV at that hospital is at least 98%. The secondary outcome is the fraction of patients cleared, compared with the naive and weighted baselines. The claim fails if $\Gamma$ estimated at one protocol hospital does not transfer to the other, meaning the two produce clearly different estimates. A coverage failure among transitional-anatomy patients also counts as a failure.
The final analysis revisits the titanium-versus-PEEK disagreement using the same bounds. Before interpreting any material effect on subsidence, we report the range of $\Gamma$ over which the effect keeps its sign. Surgeons choose cage material based partly on their own judgment of bone quality, so a sign that flips at small $\Gamma$ means the retrospective data cannot settle the dispute.
References
- Prediction of Outcome in Acute Lower Gastrointestinal Bleeding Using Gradient Boosting
- A clinically applicable AI system for detection and diagnosis of bone metastases using CT scans
- Analysis of risk factors for determining the need for prostate biopsy in patients with negative MRI
- A novel computed tomography radiomic nomogram for early evaluation of small airway dysfunction development
- A Vertebral Segmentation Dataset with Fracture Grading
- Evaluating and Correcting Performative Effects of Decision Support Systems via Causal Domain Shift
- Biomechanical Comparison of Two Intervertebral Fusions for L4-L5 Spinal Segment Using the Finite Element Methods: Titanium Alloy Versus PEEK Intervertebral Fusion Cages
- Biomechanical design of titanium-PEEK combined fusion cage based on PLIF surgical model
- VerSe: A Vertebrae labelling and segmentation benchmark for multi-detector CT images
- Diagnostic accuracy of deep learning vs. human raters for detecting osteoporotic vertebral compression fractures in routine CT scans
- A Novel Nomogram for the Prediction and Evaluation of Prognosis in Patients with Early-onset Kidney Cancer: a Population-based Study