Carrying a Patient's Airway Tree Forward Across Scanner Changes

When a patient's lungs are scanned twice, months apart and often on different machines, the second segmentation of the airway tree usually looks "worse": distal branches vanish, thin segments break, walls leak into lung tissue. Some of that loss is real disease, such as airway obliteration, mucus plugging or bronchiectasis remodeling. Much of it is not. It comes from a different scanner, a sharper or smoother reconstruction setting, thicker slices or higher noise, all of which push faint airway walls below what a segmentation network can see. Current systems segment each scan on its own. They cannot tell these two causes apart, so the follow-up tree is fragmented in ways that mean nothing clinically, and branch counts compared across visits mix biology with hardware.

We propose a follow-up segmenter that receives the patient's own earlier airway tree, aligned to the new scan, and must account for every branch of it. Each baseline branch either has to be reconstructed in the follow-up or has to be explicitly flagged as changed, and flags carry a cost. The model is trained on scan pairs where scanner and protocol differ but anatomy does not, and on pairs with simulated true branch loss. That teaches it to repair breaks caused by the scanner while leaving real disappearance visible. The underlying idea is that the patient's previous scan is the best available prior for an ambiguous low-contrast boundary, and the right way to use it is as a list of topological commitments, not as a mask to copy.

Core Claim

The claim is that topological fragmentation in follow-up scans can be cut sharply, without hiding true disease change, by a branch-level "repair or explain" objective defined on the registered baseline skeleton. Feeding the prior mask as an extra input channel does not achieve this, and neither does harmonizing scanners. Each of the four research directions plays a separate role. Topological fragmentation is the failure we target. Low-contrast boundary ambiguity is why the failure happens. Longitudinal reasoning supplies the information that resolves it. Inter-scanner variability is the stress condition that makes the problem acute and supplies the training signal, because a scanner change with no anatomical change gives a pair where every topological difference is known to be an error.

This differs from the closest existing work in a specific way. Promptable Longitudinal Lesion Segmentation in Whole-Body CT feeds a historical mask and point prompts into a U-Net as extra channels and pretrains on synthetic longitudinal pairs. That raised Dice on lesions from 53.06 (cross-sectional) to 63.71. It targets bulky lesions, has no topological term and no scanner-invariance mechanism, and its output gives no account of which prior structures disappeared. Our model outputs a segmentation together with a per-branch change probability, and the training objective links the two.

Research Program

Inputs and alignment. The inputs are a baseline CT $X_0$, its airway segmentation and skeleton graph $\mathcal{G}_0$, and a follow-up CT $X_1$. We deformably register $X_0$ to $X_1$ and warp $\mathcal{G}_0$ into follow-up coordinates. The warping follows the logic of Vascular Deformation Mapping, which tracked aortic growth by carrying baseline mesh vertices through a B-spline displacement field with sub-millimeter error. That work only handled bulky, contrast-enhanced vessels. Thin branching trees need a registration that tolerates local misalignment, so we dilate each warped branch into a tolerance tube instead of trusting voxel-exact positions.

Network. The follow-up network is a 3D U-Net, the same family as the DeepTree backbone. It takes $X_1$ plus a channel rasterizing the warped skeleton. It has two outputs: a voxel likelihood map $L$, and a change score $c_b \in [0,1]$ for every baseline branch $b$, pooled from decoder features along that branch's tolerance tube.

Objective. For each branch we compute a soft miss fraction $m_b$, which is one minus the soft-clDice topology sensitivity restricted to branch $b$. It measures how much of the warped baseline centerline the predicted mask fails to cover, using the differentiable skeletonization of clDice. The loss is

$$\mathcal{L} = \mathcal{L}_{\text{seg}}(L) + \lambda \sum_b (1 - c_b)\, m_b + \mu \sum_b \mathrm{BCE}(c_b, y_b),$$

where:

  • $\mathcal{L}_{\text{seg}}$ is the usual Dice plus clDice loss against the follow-up label;
  • $y_b$ is the change label, known exactly for synthetic pairs and set to 0 for same-patient scanner-change pairs;
  • $\lambda$ weights the topological commitment;
  • $\mu$ weights change supervision.

A branch can only be dropped cheaply if the model asserts change. That assertion is penalized when wrong, so it cannot be used as a free escape. Restricting the topological term to baseline branches keeps the cost linear in skeleton length. This avoids the cubic cost that blocks 3D use of persistent-homology losses such as TopoMatch. We keep TopoMatch's main lesson: a topological feature should only be credited where it physically overlaps its partner, and the tolerance tube enforces exactly that.

Training data. Real longitudinal airway CT with multi-scanner labels does not appear in the research file, so the primary training signal is synthetic, in the spirit of the Kirchhoff et al. pretraining. From each labeled airway CT we create a "follow-up" in two ways. The first applies scanner perturbations: resampled slice thickness, kernel-like frequency filtering, dose-dependent noise and intensity remapping. These are the factors Xue et al. show distort CT texture non-linearly. The second applies anatomical perturbations: removing or occluding distal subtrees, with the occluded lumen filled with soft-tissue intensity to mimic plugging. This reuses the synthetic-break machinery of DeepTree, but for the opposite purpose. DeepTree simulates breaks so it can always reconnect them. We simulate some breaks as true loss that must not be reconnected. Small elastic deformations stand in for breathing differences. Wherever available, real same-patient pairs supplement the synthetic data.

Baselines

Naive reference (cross-sectional, no topology). An nnU-Net-style 3D U-Net trained on follow-up scans alone with Dice plus cross-entropy. It shows how much fragmentation scanner change causes when nothing is done about it.

Strongest cross-sectional method: DeepTree. DeepTree ranked first in EXACT'09 and ATM'22. It reported 7.5% higher Tree Length Detected and 4.0% higher Branches Detected on BAS through anatomy-aware multi-class training and its breakage-reconnection module. We retrain it with the same scanner-perturbation augmentation and the same epochs and GPU budget as our model. That way any advantage we show comes from the prior, not from augmentation. For context, the ATM'22 benchmark paper reports that top models fall from about 90% Branch Detected on standard cases to about 64% on COVID-19 cases (ATM'22). We found no reported result on Lacuna for longitudinal or cross-scanner-pair airway segmentation, so there is no published number to beat on the paired task itself.

Strongest longitudinal method: prior mask as an input channel. This reimplements the promptable longitudinal design on airways. The registered baseline mask is an extra input channel, the network is pretrained on the same synthetic pairs, and clDice is added so the comparison does not reduce to "topology loss vs none."

Scanner-invariance baseline. The cross-sectional U-Net plus clDice, with the randomized-label scanner-confusion branch of Aslani et al.. In that work the confusion branch raised MS lesion Dice from 0.4540 to 0.5001 across 56 centers. Here, scanner identity is the synthetic perturbation type, or the real site where known.

Ablations isolating the key ingredient. Ablation A keeps the skeleton input channel but sets $\lambda=0$, so the change head is trained but not coupled to the topology term. Ablation B sets $\mu=0$ and removes the change head, so every baseline branch must always be covered.

What counts as beating the baselines. All methods share one train/validation/test split by patient, one tuning budget (an equal number of hyperparameter trials), and one test-time compute envelope. Winning requires both of the following:

  • a lower rate of spurious branch loss on stable cross-scanner pairs than the prior-channel baseline;
  • branch-level sensitivity to true change at least equal to the cross-sectional DeepTree baseline, which by construction is not biased toward the prior.

Why not just…?

Why not just give the network the registered prior mask, as in LongiSeg? This is the most serious threat. It may recover most of the stability gain. Nothing in the input-channel design forces the network to keep a weak branch, and nothing stops it from copying a branch that has truly disappeared. That second failure is the segmentation version of the Last Context Image trap documented in CRONOS, where copying the latest scan beats elaborate sequence models when change is small. Ablation A comes close to this baseline with the same supervision. If it matches the full model on both spurious-loss rate and true-change sensitivity, the coupling term is unnecessary and we will report that.

Why not just harmonize scanners or train for scanner invariance, then compare two independent segmentations? Invariance training helps on average, but the gains reported in Aslani et al. leave absolute performance modest. Xue et al. show that deep-learning reconstruction kernels alter images in ways standard normalization does not undo. More fundamentally, the information in a sub-voxel airway wall may simply be absent from the follow-up scan, the visibility limit that Sultan et al. stress for non-contrast coronaries. Invariance cannot restore missing signal, but a prior from a clearer scan can. The scanner-invariance baseline tests this directly on pairs where the follow-up perturbation is severe.

Why not just warp the baseline segmentation into the follow-up and union it with a fresh prediction? This gives perfect stability and zero sensitivity to loss, so it fails exactly the clinical question of surveillance. We include it as a reference point on the stability axis. It is expected to win there and lose completely on true-change detection.

Proposed Experiments

Experiment 1: controlled synthetic pairs. Using ATM'22's 500 multi-site, multi-vendor CTs, we build stable pairs (scanner perturbation only) and changed pairs (scanner perturbation plus known subtree loss). Scanner-perturbation parameters are held out from training to test zero-shot transfer to unseen "scanners." Metrics are Tree Length Detected and Branch Detected on the follow-up, the false branch-loss rate on stable pairs, and AUROC of the per-branch change score on changed pairs. As a sanity check against the cross-site shifts already in ATM'22, a second split trains on some vendors and tests on held-out vendors.

Experiment 2: real cross-site pairs as a test of synthetic realism. We pair ATM'22 scans that are acquired at different sites and differ in slice thickness but come from the same patient. If no such pairs exist, the substitute is a held-out set where one ATM'22 case is reconstructed or resampled across protocols. The point is to measure the gap between synthetic and real perturbations. If the model's advantage disappears on real shifts, the synthetic scanner model is inadequate. That would be a concrete negative finding, not a reason to drop the experiment.

Experiment 3: a label-free evaluation that sidesteps incomplete ground truth. Wang et al. note that annotators omit faint distal branches, which wrongly penalizes sensitive models. Longitudinal data offers another check. A distal branch detected independently in both scans by the cross-sectional baseline, at matching registered positions, is very unlikely to be noise. We will report agreement with this "two-visit consensus" alongside agreement with manual labels.

Experiment 4: pathological stress. We repeat Experiment 1 on the COVID-19 subset of ATM'22 to see whether the prior narrows the documented drop from about 90% to about 64% Branch Detected. We will also check whether the change head falsely attributes consolidation-induced invisibility to true loss.

Decisive check. The proposal succeeds if, on held-out scanner perturbations, two things hold together. First, the full model has a lower false branch-loss rate on stable pairs than the prior-channel baseline. Second, its change-detection AUROC is not below that of independently applied DeepTree. If the prior-channel baseline matches it on both, the key ingredient adds nothing. If our model gains stability only by losing change sensitivity, the change-flag mechanism has failed. Either outcome changes how longitudinal tubular segmentation should be built.