When the Prior Scan Is Old and Different: Change Detection for Patients Who Cannot Return Often

Radiologists rarely read a chest X-ray alone. They compare it with the patient's last one and ask whether a finding is new, stable, improving or worse. A recent family of AI models does the same thing by encoding a prior and a current image together and predicting the change between them. These models implicitly assume a particular kind of patient: one who returns often, to the same hospital, and is imaged on similar equipment. Patients far from specialist centers break that assumption. Travel burden and sparse transit push their follow-ups apart, and over a long absence the imaging equipment or protocol at the referral site often changes. For such a patient, the gap between two images contains both disease change and technical change, and a comparison model has no way to tell them apart.

We propose to measure how much current longitudinal chest X-ray models confuse acquisition change with disease change as the gap between exams grows and as acquisition conditions diverge. We then propose a targeted fix. The fix trains on pairs of images from the same patient taken close together in time but under different acquisition conditions, which serve as examples of "no clinical change." The model is taught that these pairs should look like no change, and it is made to report lower confidence when the gap is long. Geography enters as the deployment regime that produces long, mismatched gaps. Temporal drift is the mechanism that corrupts the comparison. Longitudinal reasoning is the capability we are trying to protect.

Core Claim

Longitudinal comparison models will over-call change, especially "worsening," on pairs where the prior and current images differ in view position (standing posterior-anterior versus portable anterior-posterior) and are separated by long intervals. Plain empirical risk minimization will not fix this, and neither will adding the gap and view as input features. Narrow invariance does fix it: the model's change representation is required to ignore acquisition differences in near-simultaneous same-patient pairs. This reduces false change calls on mismatched, long-gap pairs and costs little accuracy on matched pairs. The claim is specific enough to be wrong in two clean ways. Existing models may not degrade with gap or mismatch at all, or a simple metadata-conditioned model may close the gap just as well.

Grounding in Prior Work

Several papers supply the comparison architectures we build on and stress-test. BioViL-T splits an image representation into a static part, describing the current exam, and a temporal part, describing the difference from the prior. CoCa-CXR restricts attention so that each region of the current scan looks only at the matching anatomical region of the prior. TempA-VLP uses a cross-exam transformer with separate static and temporal contrastive objectives. DeltaNet subtracts prior from current feature maps outright. All four treat a feature difference as evidence of a disease difference. None conditions on, or is evaluated by, the elapsed time or the acquisition mismatch between the two images. We reuse their encoders and change the training signal and the evaluation.

Other work motivates the concern. Bordner et al. found that a sacroiliitis MRI model lost accuracy on 5- and 10-year follow-ups because scanners had improved. That model read each scan independently. We ask what happens when a model reads two scans from different technical eras jointly. Pooch et al. showed that acquisition and site differences alone can drop a chest X-ray classifier's AUROC from 0.83 to 0.68. That study was cross-sectional, and we carry the concern into within-patient pairs. The geographic literature explains why long, irregular gaps fall on rural and low-income patients. Jingchuan Guo et al. document longer driving distances combined with weaker transport options, Park et al. validate travel barriers against road networks, and Ward et al. describe rural oncology patients travelling long distances for routine care.

A third group constrains the design. Lin Guo et al. found that invariance-seeking methods failed to beat plain empirical risk minimization under temporal shift in MIMIC-IV. Their explanation was that forcing time-invariance throws away time-varying features that carry real signal. This is the strongest argument against our approach, and our response is narrow scope. We do not ask for invariance to calendar time or site. We ask for invariance only across pairs where the clinical state is approximately fixed by construction, so no real signal should be lost. Whether that holds is measured directly in the experiments below. DeepJoint shows that observation timing carries prognostic information in the ICU. We take the opposite lesson for outpatients. Visit spacing is heavily shaped by access, so we let the gap modulate confidence but never serve as evidence of stability. EMDOT supplies the evaluation discipline: chronological splits, because random splits are optimistic, and the warning that complex models can decay faster than simple ones.

Research Program

The first component is a stratified audit. Using MIMIC-CXR, we pair consecutive studies from the same patient. We record the interval between them, which is preserved under date shifting, and the view position for each from DICOM metadata. We attach change labels from two sources: the expert-annotated MS-CXR-T pairs, and the report-derived comparison relations in Chest ImaGenome that TempA-VLP used. We then evaluate BioViL-T-, CoCa-CXR- and TempA-VLP-style models in cells defined by gap length and by view match or mismatch. We report per-class error with particular attention to spurious "worsening" calls, and we report calibration. Following EMDOT, the training data precede the test data in time wherever the dataset's year-group information allows this.

The second component is null-change training. We mine same-patient pairs separated by a short interval, such as under 24 hours, that differ in view position or device. We keep only pairs whose later report states no interval change. Let $z(a,b)$ denote the temporal (change) embedding the model produces for prior $a$ and current $b$. For each such null pair $(a,b)$ we add the penalty

$$ \mathcal{L}_{\text{null}} = \lVert z(a,b) - z(b,b) \rVert^2 , $$

where $z(b,b)$ is the embedding of an image compared with itself, which defines "no change." The loss is added to each base model's usual objective with a single weight tuned on validation data. Its job is to push acquisition differences out of the change channel only, leaving the static channel, which can still use acquisition cues, untouched.

The third component is gap-aware confidence. We fit a small temperature head that takes the interval and the view-match flag and scales the change logits. Long or mismatched gaps can therefore lower confidence or trigger a "comparison unreliable, read current exam alone" output. They cannot shift probability toward "stable."

Baselines

The naive reference points come first. One predicts the majority progression class, "stable," for every pair. The other is a static classifier that sees only the current image. These set the floor and show how much the prior is worth in each gap and mismatch cell. If comparison models fall below the static model in long, mismatched cells, that alone is a finding.

The strongest existing method is CoCa-CXR. It reports 65.0% average accuracy across five conditions on MS-CXR-T progression classification, 4.8 points above BioViL-T (CoCa-CXR). For low-label settings, TempA-VLP reports 61.6% against BioViL-T's 56.3% with 10% of labels (TempA-VLP). We will reproduce these models on our chronological split and report our own reproduced numbers next to the published ones, since the split differs from the original evaluations. Null-change training is applied on top of each architecture, using the same pretraining data, the same number of fine-tuning steps and the same hyperparameter search budget. That way any gain belongs to the loss and not to extra compute.

The key competitor is metadata conditioning, described in the next section. We give it the same tuning budget as our method. Isolating ablations remove each ingredient separately: null-pair loss without the confidence head, confidence head without the null-pair loss, and null pairs that share a view position, which tests whether mismatch is what matters. Beating the baselines means three things together. First, a reduction in false "worsening" calls and in calibration error in the long-gap mismatched cells that is statistically separable, by bootstrap over patients, from the best baseline. Second, accuracy on matched short-gap pairs within one point of the unmodified model. Third, overall MS-CXR-T accuracy no worse than our reproduction of CoCa-CXR.

Why not just…?

Why not just feed the gap length and view position into the model as extra inputs? This is the most serious threat. If the model can see that the prior was a portable AP film, it might learn to discount the resulting differences without any special loss. In our view the problem is that mismatched long-gap pairs with genuine "stable" labels are rare in training data. A model given these features may simply learn a shortcut, for example "long gap means stable" or "mismatch means worse," rather than learning to separate acquisition from anatomy. That would also write access disparities directly into predictions, the risk DeepJoint's informative-observation result raises when carried over to outpatients. We test this directly. We train the conditioned model, then evaluate it with gap values shuffled within each class. A model leaning on the shortcut will lose much more accuracy than one that has learned to discount acquisition. If metadata conditioning matches our method and survives the shuffle test, we will report that and recommend it as the simpler solution.

Why not just recalibrate per gap bucket? The systematic review by Lin Lawrence Guo et al. found that recalibration restores calibration under temporal shift but not discrimination. A model that ranks a technical change above a true change will still rank it wrongly after rescaling. We include per-bucket isotonic recalibration as a baseline. We expect it to match us on calibration error but not on the rate of false "worsening" calls at a fixed sensitivity.

Why not just harmonize the images, or fall back to the static model when the gap is long? Intensity harmonization can address contrast and exposure. It cannot address the geometric and magnification differences between AP and PA views. We include histogram-matching of the prior to the current image as a baseline. A rule that falls back to the static model throws away the prior entirely. That is a reasonable floor, but it abandons exactly the patients whose care depends most on knowing whether a finding is new. The static-model numbers in the audit show what this rule costs.

Decisive Experiments

The first check can kill the project early. If accuracy and calibration of existing comparison models are flat across gap length and view-mismatch cells, the premise fails and we stop.

The second check is the main result. Null-change training should reduce spurious "worsening" calls in long, mismatched cells while leaving matched short-gap performance and overall MS-CXR-T accuracy intact. It should also outperform metadata conditioning under the gap-shuffle test. We additionally probe whether the null loss discards real signal, as Guo et al. would predict. For this we test on held-out short-interval mismatched pairs whose reports do describe change. If the model misses these, the invariance is too broad.

MIMIC-CXR records neither patient residence nor travel distance, and no external longitudinal chest X-ray benchmark appears in our sources. Within this study, therefore, gap length and acquisition mismatch stand in for the rural regime rather than measuring it. The final validation would require a partner health system with residence data and multi-site priors. There we would check whether error concentrates in patients far from the imaging center and whether our method narrows that gap.