Worst-Case Acceptance Tests for Updating ASL-to-PET Perfusion Networks

Neural networks can now turn a routine MRI scan into something close to a radioactive-tracer PET map of brain blood flow. The catch is that once such a network is cleared as a medical device, it is effectively frozen. Retraining it for a new scanner or patient population means re-certification, and a review reports that about 78% of AI medical device makers have suspended model updates for that reason (A decade of review in global regulation and research of artificial intelligence medical devices (2015–2025)). Regulators now offer an escape hatch. A predetermined change control plan is a retraining recipe, plus the test each retrained model must pass, both approved before deployment. What nobody has specified is what that acceptance test should be for a perfusion network. The obvious choice, "the new model scores at least as well on a held-out test set," is dangerous here. The patients most likely to be harmed are those whose blood arrives late in the brain, and they are the patients a held-out set represents worst.

We propose to borrow the central idea of robust wireless beamforming under imperfect channel knowledge. There, one designs for the worst case over a bounded set of plausible errors rather than for the nominal estimate. We turn that idea into a test that decides whether to accept an update. A retrained network is accepted only if its worst error against PET, searched over a small, physically defined set of acquisition and physiology perturbations, stays inside a pre-approved corridor and is no worse than the deployed model's worst case. In two sentences: nominal validation cannot detect updates that quietly break the network on slow-transit patients. A worst-case check over a handful of physiological parameters from the standard blood-flow model can detect them cheaply, and that check is concrete enough to write into a change control plan.

Background and the gap

Arterial spin labeling (ASL) measures cerebral blood flow by magnetically tagging water in arterial blood and imaging it after a wait, the post-labeling delay. When the arterial transit time is long, as in stenosis, Moyamoya disease, or small-vessel disease, a single delay catches the tag still inside the arteries. The resulting map shows false hypoperfusion and bright intravascular artifacts (Johnson et al.; Gyanwali et al.). Multi-delay ASL samples several delays and fits a kinetic model to separate flow from transit time.

Turning brain MRI into diagnostic PET goes further. It feeds single-delay ASL, multi-delay ASL, transit-time maps, and structural images into a 3D attention-gated encoder-decoder, which synthesizes ¹⁵O-water PET flow maps. It reports SSIM 0.924, PSNR 38.80 dB, correlation 0.96 with baseline PET and 0.97 after a vasodilator, and abnormal-flow detection AUC of 0.905–0.957, compared with 0.552–0.695 for raw ASL flow. This paper supplies the model we will update. It also motivates the gap: the network is trained and evaluated once, on 95 development and 15 generalization subjects, and it has no post-market adaptation or monitoring.

On the regulatory side, the review cited above and Dr. AI, Where Did You Get Your Degree? argue for certifying the learning process rather than frozen weights. FUTURE-AI notes that updates currently void clearance. These papers motivate the work but supply no technical acceptance criterion, which is what we provide.

A second strand supplies the nuisance set, and it also shows that real shifts are physiological. Cerebrovascular reactivity measurements using simultaneous 15O-water PET and ASL MRI runs acetazolamide challenges in 19 subjects. The drug shortens transit time by about 200 ms and shifts labeling efficiency by 0.7–2.4%. As a result, single-delay CVR underestimates PET by 15% ± 10%, while multi-delay CVR (40% ± 18%) matches PET (42% ± 19%). These quantities are exactly the low-dimensional, physically bounded perturbations along which a deployed network is likely to break.

The method comes from Distributed Robust Multicell Coordinated Beamforming With Imperfect CSI. That paper shows that beamformers designed on the nominal channel estimate collapse to about 5 dB SINR against a 20 dB target once estimation error is present, whereas enforcing constraints over a bounded error set holds the target. We adopt that design stance but not its machinery. The S-lemma reformulation it uses needs quadratic structure, and a convolutional network does not have it. We therefore replace a proof with dense search over a low-dimensional set.

Core Claim

Let $\theta$ be a vector of nuisance parameters and $\mathcal{U}$ the approved box of values it may take. The components of $\theta$ are a transit-time shift, a labeling-efficiency scale, blood $T_1$ (a function of hematocrit), which delays were acquired, and a noise level. For each held-out subject $s$, a forward kinetic model (the general kinetic model for pseudo-continuous ASL) regenerates that subject's ASL inputs $x_s(\theta)$ from their fitted flow and transit maps. The subject's own PET map $y_s$ remains the target. A candidate network $f_{\text{new}}$ replacing the deployed $f_{\text{old}}$ is accepted if

$$\max_{\theta \in \mathcal{U}} \frac{1}{|S|}\sum_{s \in S} L\big(f_{\text{new}}(x_s(\theta)), y_s\big) \le \min\Big(\tau,\ \max_{\theta \in \mathcal{U}} \frac{1}{|S|}\sum_{s\in S} L\big(f_{\text{old}}(x_s(\theta)), y_s\big) + \delta\Big).$$

Here $L$ is the voxel error inside regions of interest, $\tau$ is the pre-approved corridor, and $\delta$ is a small allowed slack. The claim is that this test rejects updates that degrade slow-transit patients, and that a nominal held-out test accepts those updates.

The set $\mathcal{U}$ has about five dimensions, so the maximum can be found by dense grid search followed by local refinement. The result is an empirical worst case, not a certificate. We state that plainly in the change control plan.

Research Program

We first build the perturbation generator. For each subject in the hybrid PET/MRI cohort of Turning brain MRI into diagnostic PET, we fit flow and transit maps from multi-delay ASL. We then re-synthesize the ASL inputs under shifted $\theta$ and add noise matched to the delay count. We validate the generator on the acetazolamide cohort: applying the measured transit-time and labeling-efficiency shifts to pre-drug data should reproduce the direction and rough size of the observed changes in the post-drug ASL.

We then reproduce the 3D attention network as $f_{\text{old}}$. Next we simulate a deployment stream of site and protocol changes: a site that drops to two delays, an older memory-clinic-like population with long transit times, and a noisier scanner. The long-transit population is motivated by the 22% higher spatial coefficient of variation and the 23% ASL exclusion rate in Cortical microinfarcts in memory clinic patients. At each change, we produce many candidate updates by fine-tuning on small new-site batches under varied learning rates, epochs, and replay fractions. This gives a population of updates, some beneficial and some harmful.

We label each candidate using data the gate never sees: the 15-subject generalization set, the post-acetazolamide PET scans, and held-out long-transit subjects. A candidate counts as harmful if its error on any of these real shifted sets exceeds that of $f_{\text{old}}$.

As a limited check that the test is not specific to neuroimaging, we will repeat the protocol on a district-heating controller. Pipe transport delay plays the same role there as arterial transit time: an unmeasured lag that a nominal policy mistakes for a change in demand. We will use the 20-user network of Using Flexibility Envelopes for the Demand-Side Hierarchical Optimization of District Heating Networks, which is built on public NREL building models and TMY3 weather, with $\mathcal{U}$ spanning transport delay and building thermal constants and the ±2 °C comfort band as the corridor. This is a secondary replication, not the core claim.

Baselines

The do-nothing reference is the frozen $f_{\text{old}}$, never updated. It represents the 78% of manufacturers who suspend updates. Every accepted update policy must beat it on the real shifted sets, or updating has no point.

The main competitor is the standard change control plan: retrain on new-site data and accept if nominal held-out SSIM, PSNR, and PET correlation do not drop. This is what the review describes as current practice, so it is the policy our test must beat. It will use the same candidate pool, the same held-out subjects, and a threshold tuned to give the same overall acceptance rate as our gate. That tuning makes the comparison about which updates get accepted, not how many.

We also run an augmentation-trained update with nominal acceptance. Here candidates are fine-tuned with random kinetic perturbations drawn from the same $\mathcal{U}$, under the same compute budget.

The strongest reported performance for the task itself is the 3D attention network of Turning brain MRI into diagnostic PET: SSIM 0.924, PSNR 38.80 dB, and AUC 0.905–0.957. Our reproduction must land near those numbers before any update study is meaningful. The 2D U-Net's reported SSIM of 0.862 bounds how much a reproduction may fall short.

The physics-only reference is multi-delay kinetic fitting with no learning, which reports CVR matching PET in the acetazolamide study.

The key ablation replaces the maximum over $\mathcal{U}$ with an average over random draws from $\mathcal{U}$. This isolates whether the worst-case framing matters, as distinct from simply testing on perturbed inputs.

Our gate beats the nominal plan if, at matched acceptance rate, it accepts significantly fewer harmful updates. We will judge significance with a paired bootstrap over candidates. It must also leave the long-transit group's AUC for abnormal-flow detection no lower than the frozen model's.

Why not just…?

Why not just validate updates on a larger held-out set? A larger set helps only if it contains enough long-transit and atypical-physiology patients, and those patients are the ones most often excluded from ASL cohorts. One cohort excluded 23% of subjects (Cortical microinfarcts in memory clinic patients). The matched-acceptance-rate comparison above measures this directly. If nominal validation catches harmful updates as often as our gate does, the proposal fails, and we will report it that way.

Why not just train with physics-based augmentation and skip the gate? This is a real threat. Augmentation may make most updates robust, in which case the gate rarely fires. The two address different jobs, though: augmentation is a training choice, while a change control plan needs an acceptance test that also works for updates that are not trained that way. The augmentation baseline shows how much harm remains after augmentation. If that remaining harm is negligible, the contribution shrinks to "approve augmentation in the plan," which is still worth stating.

Why not just use multi-delay kinetic fitting and avoid learned models altogether? For global reactivity, kinetic fitting already matches PET (Cerebrovascular reactivity measurements using simultaneous 15O-water PET and ASL MRI). For focal abnormality detection, however, raw ASL reaches only 0.552–0.695 AUC against 0.905–0.957 for the network (Turning brain MRI into diagnostic PET). We report kinetic fitting alongside the network so that readers can see where learning is actually needed.

Why not just trigger retraining on a spatial-variance drift monitor? A high spatial coefficient of variation does track long transit times, but it tells you when to retrain, not whether the result is safe to deploy. We will include it as the trigger in both arms of the comparison.

Proposed Experiments

The decisive experiment is the candidate-update study. At matched acceptance rate, we compare the harmful-accept rate and beneficial-reject rate of three tests: the nominal test, the average-case ablation, and the worst-case gate. We score them against real shifted PET, specifically post-acetazolamide scans and long-transit held-out subjects, which the gate never sees.

A second check asks whether the synthetic worst case predicts real failure. Across candidates, we compute the rank correlation between each candidate's gated worst-case error and its error on post-drug PET. A weak correlation would mean the kinetic generator does not capture real shift, and it would falsify the approach.

Third, we vary the box size $\mathcal{U}$ to trace the trade-off between conservatism and adaptivity, the same trade-off that motivates distributionally robust formulations in Distributionally Robust Optimization for Aerial Multi-Access Edge Computing.

Finally, the district-heating replication reports comfort violations and energy use of gated versus nominally accepted controller updates. No result is reported on Lacuna for gated updates in that setting. The nearest reference points are the 0.545 °C comfort error and 2.19% energy saving of the DRL controller in Towards Optimal District Heating Temperature Control in China with Deep Reinforcement Learning, which we cite for context only.

The main risks are access and sample size. The hybrid PET/MRI and acetazolamide cohorts require collaboration, and 19 challenge subjects give limited statistical power for subgroup claims.