Imaging models for watched-but-untreated lesions are trained and scored against tissue. Examples include prostate cancers on active surveillance, pancreatic cysts and small thyroid nodules. The tissue, however, is not sampled at random. A biopsy is ordered when a clinician sees something worrying on the scan or in a blood test, and patients who look fine are biopsied rarely or never. The "ground truth" is therefore partly a record of what past clinicians already believed from the same images. A model that learns to spot what triggered biopsies can look excellent without predicting biological progression any better than the people who ordered the test. Patients who were never biopsied are often labeled benign because they stayed stable for a fixed number of years. This quietly drops everyone who died, moved, or was followed too briefly.
This note proposes treating the histological label in surveillance cohorts as an incompletely observed event, not a fixed answer. The time at which tissue is sampled is a recorded clinical decision. We model that decision from the imaging and lab history the clinician saw, and we use the model to reweight the evidence each biopsy provides. Stable-without-biopsy is treated as "not yet progressed, last checked at time t," not as "benign." The hypothesis has two parts. First, the standard labeling recipes inflate apparent accuracy for exactly the imaging features that drive biopsy orders. Second, this distortion can be measured and largely removed using a subset of biopsies that were scheduled by protocol rather than triggered by findings.
Core Claim
In a surveillance cohort, the observed outcome for each patient is an interval: progression happened somewhere between the last benign biopsy and the first upgraded one, or after the last benign one if none was upgraded. How dense and how timely those intervals are depends on clinical behavior. The claim is that two common practices bias both training and evaluation in a predictable direction. One is dating the event at the biopsy. The other, used by Cyst-X, assigns benign status after at least three years of follow-up. The bias favors features correlated with biopsy triggers, because those patients are sampled earlier and more often, so their progression is detected sooner.
If clinicians order biopsies based on information that is recorded (prior scans, scores such as PI-RADS, PSA trends), the verification process is "ignorable given history." It can then be corrected by inverse-probability weighting that changes over time, combined with an interval-censored survival likelihood. The new element is not a new architecture. It is building the verification decision into the learning and evaluation target, with a built-in validation anchor: biopsies scheduled by calendar, independent of findings.
Research Program
The motivating evidence comes from two places. The first is the active-surveillance literature. Its synthesis in An et al. shows that MRI-targeted biopsy reclassifies a substantial share of "low-risk" men, so where and when you sample changes the label. The second is the dynamic-survival work of Dynamic-DeepHit-Lite, a recurrent survival model that updates risk as new PSA, MRI and repeat-biopsy results arrive. It reports C-index 0.79 (±0.11) at a 3-year horizon and 0.82 (±0.08) at 5 years, against 0.67 and 0.73 for a baseline Cox model. Dynamic-DeepHit-Lite supplies the method we build on. It also treats biopsy results as the outcome without asking why those biopsies happened, and that is the gap we target.
The same omission runs through the image-to-pathology datasets. ThyUS2Path pairs thyroid ultrasound with surgical pathology from operated patients only. CMMD pairs mammograms with core-needle biopsy from biopsied women only. The longitudinal bpMRI foundation model, a vision transformer fine-tuned on paired yearly prostate MRIs, kept only the 206 patients who had complete scan pairs.
We will build three components. The first is a verification model. At each surveillance visit $k$ it estimates the probability $\pi_{ik}$ that patient $i$ is biopsied, given everything observed up to that visit: prior images through a frozen image encoder, radiologist scores, PSA history, time since last biopsy, and whether the visit falls on the protocol schedule. The second is an interval-censored progression model. It uses the same dynamic backbone as Dynamic-DeepHit-Lite and is trained with a weighted likelihood:
$$\mathcal{L}=\sum_i w_i\,\log\big[S(L_i\mid h_i)-S(R_i\mid h_i)\big],\qquad w_i=\prod_{k\in\mathcal{B}_i}\frac{1}{\pi_{ik}}.$$
Here $S(t\mid h_i)$ is the predicted probability of remaining unprogressed past time $t$ given patient $i$'s history $h_i$. $L_i$ is the time of the last non-upgraded biopsy, $R_i$ is the time of the first upgraded biopsy ($R_i=\infty$ if none), and $\mathcal{B}_i$ is the set of visits at which patient $i$ was biopsied. Weights are stabilized and truncated, as is standard.
The third component is a support check. It borrows the idea of Target Population Identification, which predicts only for individuals who resemble the study cohort and abstains on the rest. We report horizon-specific risk only for patients whose biopsy probabilities are bounded away from zero within the follow-up window. The same check enforces the limited-follow-up constraint: the model declines to issue 5-year risks where observed follow-up and biopsy coverage cannot support them, rather than extrapolating.
Dropout from surveillance is a separate censoring process. It is plausibly dependent on health, because sicker patients leave or die. We handle it as a sensitivity layer using the dependent-censoring copula approach of Gharari Foomani et al.. That method couples a deep survival model with a Clayton or Frank copula linking event and censoring times. We sweep the dependence parameter rather than claim to identify it. Unmeasured biopsy triggers, such as undocumented frailty or a clinician's gut feeling, cannot be removed by any weighting. We bound their effect with a sensitivity parameter that scales the odds of biopsy among patients who later progressed, and report how much the conclusions move.
Baselines
The naive reference point is the common practice. Train and score the same dynamic backbone with biopsy-upgrade as the event dated at the biopsy, and with unbiopsied stable patients either censored at last contact or labeled benign after a fixed stable window, the latter mirroring Cyst-X. This is what we expect most published surveillance models to effectively do. It is the number the proposal must show to be miscalibrated.
The strongest existing method is Dynamic-DeepHit-Lite, reimplemented with its published inputs. Its reported C-index is 0.79 (±0.11) at 3 years and 0.82 (±0.08) at 5 years on its single-center cohort of 585 men. It is the strongest competitor because it already uses the longitudinal biopsy and imaging stream we use. Any gain from our approach must come from handling verification, not from more data or capacity.
On the image side we also run the bpMRI multi-scale foundation model. It reports case-level progression AUROC 0.727, against 0.745 for radiologists and 0.720 for a Res-UNet. Its encoder is our image feature extractor, so the image component is identical across arms. For the clinical-guideline reference we report radiologist scores alone. All arms share the same patients, folds, backbone, input features and hyperparameter search budget. The only differences are label construction and weighting.
Two ablations isolate the key ingredient. One drops the weights but keeps interval censoring, separating the effect of honest interval labels from the effect of verification correction. The other keeps the weights but fits a verification model that ignores imaging, which tests whether image-driven biopsy triggering is the source of bias.
Beating the strongest baseline does not mean a higher C-index on triggered-biopsy labels. We may well lose there, and that would be informative. Beating it means two things on the protocol-scheduled evaluation subset described below. The first is lower calibration error, measured by integrated Brier score and horizon-specific calibration slope. The second is a smaller gap between the C-index estimated on all labels and on the protocol subset. The bar is a calibration slope whose confidence interval covers 1 where the baseline's does not.
Why not just…?
Why not just train and evaluate only on protocol-scheduled biopsies? This is the real threat. If scheduled biopsies are plentiful, restricting to them removes trigger bias by design, with no weighting model at all. Its weakness is sample size and coverage. Scheduled biopsies typically thin out in later surveillance years, and patients who progress early leave the schedule through triggered biopsies, so the scheduled subset under-represents fast progressors. We will run it as a full arm. If it matches the weighted model on held-out scheduled biopsies and on the simulation recovery test, we will recommend it as the cheaper recipe and reframe the contribution as the measurement of bias.
Why not just label stable patients as benign after enough years, as Cyst-X does? That rule conditions inclusion on remaining in follow-up long enough. The file documents this pattern of conditioning on the future in Cui, Shu et al., whose small-airway model required a repeat lung test at least a year later, and in Yang et al., whose 3–6 month window missed later atrial fibrillation recurrences. The rule also cannot use patients who are followed for less than the fixed window. It is our naive baseline, and the simulation experiment measures exactly how much it distorts estimates of full-population accuracy.
Why not just apply standard propensity weighting once at baseline? Sample Selection Bias in Machine Learning for Healthcare reports that ignoring selection costs up to 22% AUC. It also reports that forcing global distribution alignment can hurt when shifts are large, which constrains our design. Verification in surveillance is a sequence of decisions driven by evolving images, so a single baseline propensity cannot represent it. We answer that warning with visit-level weights, weight truncation and the abstention check. A static-weighting arm is included so the comparison is direct.
Why not just use a censoring-aware survival model such as SALaD? SALaD splits patient representations into event, censoring and shared latent parts. It wins 109 of 156 comparisons on tabular survival benchmarks. It models when follow-up ends, not whether and when the label was observed, and it assumes event and censoring times are independent given covariates. We run it as a baseline for the dropout process. We expect it to be complementary to, not a substitute for, verification modeling.
Proposed Experiments
The first experiment is a controlled recovery test on public, fully verified data, in the semi-synthetic style of the selection-bias paper above. In CMMD and the thyroid ultrasound dataset behind ThyUS2Path, every case has tissue. We impose an artificial verification policy that reveals labels with probability rising in a radiologist-like score computed from the images. We also impose artificial follow-up truncation. Each labeling recipe is then judged by how closely it recovers the AUROC and calibration obtained with all labels revealed. ThyUS2Path's reported external AUROC of 0.70–0.79 gives the scale of the full-label reference; CMMD has no reported model result in the file. These datasets are already biased toward biopsied patients, so this experiment tests recovery from a second, known selection. It does not test recovery of the real screening population.
The second and decisive experiment uses real surveillance cohorts. Candidates are the structured active-surveillance cohort behind Dynamic-DeepHit-Lite and the Miami trial behind the bpMRI model, both obtained through collaboration, with secondary transfer to multicenter cyst MRI like Cyst-X. Biopsies are split by whether they were protocol-scheduled or finding-triggered, and only triggered and unscheduled data are used for training. The test is whether the naive recipe's apparent accuracy drops on scheduled biopsies while the weighted model's holds. A further check is whether the drop is concentrated in the imaging features the verification model ranks as strongest biopsy triggers.
If the gap is absent, trigger bias is negligible in that cohort. That would be a useful negative result validating current practice. If the gap is present and the weighted model closes it, while the image-blind verification ablation does not, the proposal's central claim holds. A final sensitivity analysis sweeps the unmeasured-trigger parameter and the copula dependence parameter. It reports the smallest hidden effect that would overturn the conclusion, so readers can judge whether such an effect is clinically plausible.
References
- Cyst-X: AI-Powered Pancreatic Cancer Risk Prediction from Multicenter MRI in Centralized and Federated Learning
- Multiparametric Magnetic Resonance Imaging for Active Surveillance of Prostate Cancer
- Developing machine learning algorithms for dynamic estimation of progression during active surveillance for prostate cancer
- An ultrasonography of thyroid nodules dataset with pathological diagnosis annotation for deep learning
- An Online Mammography Database with Biopsy Confirmed Types
- Predicting Prostate Cancer Progression During Active Surveillance Using Longitudinal bpMRI Scans and A Multi-scale Foundation Model
- Sample Selection Bias in Machine Learning for Healthcare
- Copula-Based Deep Survival Models for Dependent Censoring
- A novel computed tomography radiomic nomogram for early evaluation of small airway dysfunction development
- A predictive model using left atrial function and B‐type natriuretic peptide level in predicting the recurrence of early persistent atrial fibrillation after radiofrequency ablation
- Explicitly Modeling Censoring Produces Superior Survival Predictors