A CT or MRI scan is a 3D volume made of hundreds of 2D slices. In most labeled clinical datasets, though, only a few slices carry text or masks: the ones a radiologist chose to bookmark, measure, or describe in the report. Those chosen slices are not a random sample. They tend to show the lesion at its largest, clearest, highest-contrast cross-section. The slices that show the lesion's edges, its faint tails, and its contact with neighboring tissue are almost never labeled. Models trained on 2D slices learn from the chosen slices and are scored on them. As a result, published 2D results may overstate how these models perform across the full volume, which is the setting a model meets when it scans a whole study on its own.
This proposal treats the radiologist's choice of which slice to label as a self-disclosure process. The term comes from social-media health research, where models trained only on people who publicly announce a diagnosis learn the traits of people who announce, and those people are not representative of all patients. The imaging case differs from the social-media case in one way that makes it worth studying. A social-media user who never discloses is never observed. An unlabeled slice, by contrast, is present in the volume, just without a label. So the selection bias can be measured with a small audit, and it can be corrected with standard missing-data tools. We propose to quantify this "disclosure gap" for 2D segmentation and vision-language pipelines, and to test whether correcting for it with an audit closes the gap better than the simpler 2.5D and adaptation fixes that a reviewer would reach for first.
Core Claim
Two failures are usually discussed separately: the 2D treatment of 3D scans (volumetric context loss), and training on selectively disclosed labels. Here they are one failure. The slices that have labels are a non-random subset of each volume, chosen on visible image properties such as lesion area, contrast, and how central the slice is. Performance measured on those slices therefore systematically overestimates performance on the rest of the volume.
We make three claims. First, this gap is large and measurable within the same lesion, by comparing chosen slices with their own neighbors. Second, because the unlabeled slices are observed, the gap can be estimated without bias from a small, uniformly sampled audit set of off-key slices. This is the imaging counterpart of a representative survey supplement, and the social-media setting cannot produce one. Third, training that reweights or pseudo-labels slices according to how likely each slice was to be chosen should improve whole-volume accuracy more than adding neighboring slices uniformly.
The motivating evidence comes from both directions. On the imaging side, A Unified 2D Framework for DeepLesion Detection, Segmentation and Short Report Generation builds a detect-then-crop-then-segment pipeline on DeepLesion CT slices. It reports Dice 62.6% against 34.1% for nnUNet. It also names two limitations: the discarded 3D context, and the fact that a missed detection prevents any later stage from running. Our question is what that 62.6% means once you leave the chosen slice. Enhancing vision-language models for medical imaging: bridging the 3D gap with innovative slice selection introduces Vote-MI, an unsupervised method that clusters slice features to pick representative slices for a vision-language model. Its benchmark, BrainMD-select, scores a selector by agreement with radiologist-chosen slices (59.4% within five slices, against 28.2% for random). That metric rewards reproducing the disclosure process. Our proposal reads it as a direct measurement of the selection mechanism.
On the disclosure side, The role of personality, age, and gender in tweeting about mental illness and Social media language of healthcare super-utilizers show that the people who disclose differ systematically from those who don't. The disclosers are more neurotic, post twice as often, and use more distressed language. These papers supply the conceptual model we reuse: selection based on observable traits. They also mark the limit we exploit, which is that in social media the silent group cannot be audited.
Research Program
The program has three parts.
A disclosure-propensity model. For each slice $s$ in a volume, define the disclosure propensity $e(s)$ as the probability that the slice is the labeled or reported one, given features computable from the unlabeled volume. These features are a slice's lesion-area profile, its local contrast, its distance from the slice with the maximum lesion cross-section, and its body region. We estimate $e(s)$ on BrainMD, where radiologist choices are recorded, and on DeepLesion key slices.
One check is required before relying on DeepLesion. We believe DeepLesion annotations derive from radiologist bookmarks, but the research file does not document this. We will confirm it from the dataset documentation before treating DeepLesion key slices as disclosures.
An audit set that guarantees coverage. Radiologists may choose slices almost deterministically, for example always the maximum-diameter slice. In that case $e(s)$ is near zero for most slices, and pure inverse-propensity weighting fails. That failure is the correct diagnosis, not a reason to avoid weighting. The fix is design-based. We will annotate a small audit set of off-key slices, sampled uniformly within each lesion's 3D extent. We use 3D masks where they exist: BTCV and AMOS organ labels, the 3D masks in the ULS23 release of DeepLesion, and any additional cases where we can annotate ourselves. On this audit set, the inclusion probability is known by construction.
A doubly robust estimator and training objective. "Doubly robust" means an estimate that stays correct if either the pseudo-labels or the inclusion probabilities are accurate, so it does not depend on both being right. Let $\hat m(s)$ be a pseudo-label obtained by propagating the key-slice mask through the volume. Propagation uses a volumetric model, for example a 3D or bidirectional state-space model in the style of Swin-UMamba: Mamba-based UNet with ImageNet-based pretraining. Let $\ell$ be the per-slice loss, $f$ the 2D model, $y(s)$ the true mask, $A$ the audit set, and $\pi(s)$ the known audit inclusion probability. The whole-volume risk is estimated as
$$\hat R(f) = \frac{1}{|V|}\sum_{s \in V} \ell\big(f(s), \hat m(s)\big) + \frac{1}{|V|}\sum_{s \in A} \frac{1}{\pi(s)}\Big[\ell\big(f(s), y(s)\big) - \ell\big(f(s), \hat m(s)\big)\Big],$$
where $V$ is the set of slices within the lesion's extent. The first term lets dense pseudo-labels reach every silent slice. The second term removes the pseudo-labels' bias using the audit set. We use the same quantity in two roles: as an unbiased evaluation metric (with $f$ fixed) and as a training objective.
The vision-language side is a smaller, parallel study. Your other Left! Vision-Language Models Fail to Identify Relative Positions in Medical Images shows that models fall back on "textbook" anatomy when the visual evidence is weak. GPT-4o drops from 75% to 50% on flipped scans and rises to 87.4% when organ names are replaced by letters. We test whether this fallback is stronger on low-propensity slices, where the visual evidence is atypical. That would connect textbook bias to disclosure bias.
Baselines
The naive reference point is the standard protocol: train on disclosed key slices and report Dice on disclosed key slices. For DeepLesion, the strongest existing number in our file is the Search-and-Segment pipeline of A Unified 2D Framework for DeepLesion Detection, Segmentation and Short Report Generation, at Dice 62.6%. We will re-run that pipeline on our own splits so that the key-slice number reproduces near 62.6%, and then evaluate it on the audit set. "Beating" this baseline does not mean a higher key-slice Dice. It means a higher audit-set (whole-volume) Dice, with key-slice Dice no more than one point lower.
The strongest competitor for the training objective is the 2.5D approach: add the neighboring slices of each key slice with propagated pseudo-labels, all weighted equally. This isolates our key ingredient, since it uses the same pseudo-labels, data, architecture, and tuning budget, but no audit correction and no propensity information. The ablation that isolates the propensity component removes the second term of $\hat R$ but reweights pseudo-labeled slices by $1/e(s)$.
For slice selection in the vision-language experiments, the baselines are random selection (28.2%) and Vote-MI (59.4% on BrainMD-select, from Enhancing vision-language models for medical imaging: bridging the 3D gap with innovative slice selection). We compare them on BrainBench accuracy when slices are drawn across propensity deciles, not on agreement with radiologists.
The domain-adaptation baseline treats disclosed and undisclosed slices as two domains and aligns their feature distributions with quantile alignment, following DNN-FATC from Cross-Domain Depression Detection via Harvesting Social Media. That method reports F1 78.5% on Twitter-to-Weibo transfer; we found no reported result on Lacuna for it on imaging data.
All methods share the same backbone, the same training budget in GPU-hours, and an equal number of hyperparameter trials. Tuning is done on a validation audit set disjoint from the test audit set.
Why not just…?
Why not just train a native 3D segmenter on full volumes? The labels are the problem, not the architecture. A 3D model trained with loss only on disclosed slices, or on masks propagated from them, still learns most strongly where the radiologist looked. Reporting its Dice on key slices hides this in the same way. Deep convolutional networks for pancreas segmentation in CT imaging and ProMISe: Promptable Medical Image Segmentation using SAM show that 2D processing loses information across slices, but neither addresses where the supervision comes from. We include a 3D model trained on sparse labels as an extra arm, and evaluate it with the same audit-set estimator.
Why not just add neighboring slices uniformly (2.5D)? This is the real threat. If pseudo-label propagation is accurate, uniform inclusion may capture most of the gain, and the audit correction would add little. The experiment settles this directly. We measure the gap between uniform 2.5D and the doubly robust objective on audit-set Dice, stratified by distance from the key slice. If the gap is within noise across all strata, we will report that the bias is real but cheaply fixed. The proposal's contribution would then narrow to the measurement protocol.
Why not just use a better slice selector such as Vote-MI? Vote-MI fixes which slices a model sees at inference time. It is scored by agreement with radiologists, so a perfect score means perfectly reproducing the disclosure bias. It does not change what the model was trained on. It also cannot tell us how the model behaves on slices a radiologist would skip.
Why not just align disclosed and undisclosed slice features with domain adaptation? Aligning feature distributions assumes the label relationship is the same in both domains. At lesion margins it is not: a partial-volume boundary slice looks different and also has a different correct mask. Its divergent-feature component exists precisely because the same behavioral feature can mean opposite things on different platforms (for example, posting activity is lower for depressed Twitter users but higher for depressed Weibo users), so the analogy cuts both ways. We run the alignment baseline and expect it to help on distribution statistics but not on boundary Dice.
Proposed Experiments
Controlled simulation. On BTCV and AMOS, which have full 3D masks, we impose a synthetic disclosure rule: label only the maximum-area slice of each structure, with propensities ranging from soft to deterministic. Because the truth is known everywhere, this tests whether the estimator $\hat R$ recovers whole-volume Dice. It also tests the failure of pure inverse weighting in the deterministic case, and how large the audit set must be. We will vary it from roughly 2% to 20% of off-key slices.
DeepLesion disclosure gap. On real data, we run the reproduced Search-and-Segment pipeline on the DeepLesion audit set. We report Dice as a function of distance from the key slice, and also the missed-detection rate, which captures the cascade failure the original authors identify. We consider the disclosure gap confirmed if audit-set Dice falls well below the key-slice Dice that reproduces near 62.6%.
BrainMD propensity study. We fit $e(s)$ to radiologist choices and test whether BrainBench zero-shot accuracy decreases with lower propensity. We also test whether Vote-MI's gains over random selection shrink once evaluation is spread evenly across propensity deciles.
Textbook bias on silent slices. We build MIRP-style relative-position questions from off-key slices. We test whether the gap between the organ-name and letter-marker conditions widens as propensity falls.
Decisive check. The proposal rests on the doubly robust objective beating uniform 2.5D on test audit-set Dice, at matched compute, consistently across three seeds. If it does not, the result still stands as a demonstration that 2D medical benchmarks report performance on a disclosed subset, together with a low-cost audit protocol for measuring it.
References
- A Unified 2D Framework for DeepLesion Detection, Segmentation and Short Report Generation
- Enhancing vision-language models for medical imaging: bridging the 3D gap with innovative slice selection
- The role of personality, age, and gender in tweeting about mental illness
- Social media language of healthcare super-utilizers
- Swin-UMamba: Mamba-Based UNet with ImageNet-Based Pretraining
- Your other Left! Vision-Language Models Fail to Identify Relative Positions in Medical Images
- Cross-Domain Depression Detection via Harvesting Social Media
- Deep convolutional networks for pancreas segmentation in CT imaging
- ProMISe: Promptable Medical Image Segmentation using SAM