Clinicians increasingly receive "brain growth chart" reports. A normative model, meaning a statistical model of how a brain measure is distributed in healthy people as a smooth, non-linear function of age and sex, turns each patient's scan into z-scores: how unusual each region is for someone of that age. The trouble is that almost everyone looks unusual somewhere. In a large psychosis-risk cohort, 74.6% of at-risk individuals had at least one cortical region in the bottom 5% for thickness, and so did 71.7% of healthy controls (Normative modeling of brain morphometry in Clinical High-Risk for Psychosis). A report that flags something in nearly every healthy person gives a clinician nothing to act on.
We propose to bring the logic of cluster-based permutation testing to a single patient. Cluster-based permutation testing is a standard neuroimaging method that declares a finding only when a spatially contiguous patch of signal is larger than what reshuffled data produce. Our version asks a different question from "is any region abnormal?" It asks whether this patient's map contains a contiguous patch of deviation larger than the biggest patch seen in age-matched healthy people who were held out of model fitting. Ranking the patient among those held-out people gives an exact, finite-sample false-alarm rate for the whole cortex. The prediction is that scattered single-region deviations, which are common in healthy people, will mostly not reach significance, while spatially coherent deviations will, and that the latter carry the diagnostic and prognostic signal.
Core Claim
The claim has two parts. The first is about method. Replacing "count of infranormal regions" with "maximum cluster mass, calibrated against held-out age-matched controls" turns a normative report into a statement with a guaranteed per-patient false-positive rate. The guarantee holds under spatial autocorrelation and under age-dependent changes in that autocorrelation, because the null comes from real healthy deviation maps rather than from an independence assumption.
The second part is empirical. This statistic should separate clinical groups where region counts fail, and it should do so most clearly at the ends of the lifespan, where the non-linear age model matters most. Concretely, write $Z_{iv} = (y_{iv} - \hat\mu_v(x_i))/\hat\sigma_v(x_i)$ for subject $i$'s deviation at cortical vertex or parcel $v$, where $\hat\mu_v$ and $\hat\sigma_v$ are the fitted non-linear normative mean and spread given covariates $x_i$ (age, sex, site). We take suprathreshold vertices ($Z_{iv} < -u$), join neighbours on the cortical adjacency graph into clusters, and define the subject's statistic as the largest cluster's summed deviation:
$$M_i = \max_k \sum_{v \in C_{ik}} |Z_{iv}|.$$
Let $\mathcal{C}(x_i)$ be the set of held-out healthy controls in an age neighbourhood of subject $i$. The patient's p-value is
$$p_i = \frac{1 + \#\{j \in \mathcal{C}(x_i): M_j \ge M_i\}}{|\mathcal{C}(x_i)| + 1}.$$
If the patient is exchangeable with those controls, this p-value is exactly valid. Exchangeability here means the patient is indistinguishable from a healthy person of that age, so they are interchangeable for the purpose of the test. This is the same rank argument that makes permutation tests exact, with healthy subjects playing the role of shuffled labels.
Relation to Prior Work
The method draws on three lines of work. Cluster-mass permutation inference, as implemented in MEG and EEG data analysis with MNE-Python and applied to adjacency lattices in Sawalma et al., supplies the clustering and max-statistic logic. It was built for group contrasts, though, and offers no way to score one patient. We keep the max-statistic but move exchangeability from condition labels to subjects. That move also replaces the arbitrary extent thresholds of earlier two-threshold rules such as van Veen et al. with an empirical null. Combrisson et al. show that independence-based corrections erase diffuse effects in autocorrelated data, which motivates the max-statistic over Bonferroni.
Non-linear normative modeling supplies $\hat\mu$ and $\hat\sigma$. Brain charts for the human lifespan fit GAMLSS curves (a regression family that models a measure's mean, spread and shape as smooth functions of age) to global and regional phenotypes. PyNM (PyNM) packages similar models for tabular regions. Both stop at per-region centiles and do not combine deviations spatially. Deep normative models take a different route and compress deviation into one number. Breaking the Norm uses latent reconstruction error, FAAE an adversarial autoencoder, and an enhanced conditional VAE samples synthetic healthy profiles. None of these attaches a calibrated false-alarm rate to the individual report. Our proposal is agnostic to the normative backbone and adds the calibrated spatial test on top.
Partial correlation acts here as a constraint and as an audit tool rather than as the method itself. A z-score is a residual after removing age, which makes it a partial residual. If the age model is linear, as in standard residualization, curvature in age leaks into the residual. This matters most where trajectories bend sharply, for example the infant cortical expansion documented by Li et al.. We therefore test, in healthy held-out data, that both $Z_{iv}$ and $M_i$ have zero partial correlation with age after a flexible spline adjustment. Ernst et al. used the same device to show that summarization metric correlations were artifacts of text length. Wang et al. (2025) constrain the design. They show that label permutation with covariates collinear to the predictor can collapse power. Patient groups are often older than controls, which creates exactly that collinearity. Calibrating against age-matched controls avoids permuting diagnosis against a correlated covariate.
Research Program
We will build three things. The first is a vertex-wise (or, for consortium data, parcel-wise) normative model of cortical thickness, fit on one split of healthy data with site harmonized as in Schabdach et al.. The second is an age-binned calibration bank of healthy cluster masses. We will use local age windows, because the size of the largest healthy cluster depends on how spatially smooth the deviation maps are, and that smoothness changes with age. The third is a per-patient report: the p-value, the location of the significant cluster, and its extent. This report is the translational product. It makes a falsifiable, interpretable claim, "a contiguous temporal-lobe thinning this large occurs in under 2% of healthy people your age," rather than an uncalibrated score.
Henry et al. found that clinicians build trust through experience rather than internal model explanations. A report whose false-alarm rate can be checked against their own healthy patients suits that kind of trust-building. The cluster-defining threshold $u$ is the known weak point of cluster inference. We will either fix it in advance or integrate over a grid of thresholds and calibrate the combined statistic in the same way.
Baselines
The naive reference point is the region-count rule of Haas et al.: flag a person if any region has $Z < -1.64$. It reported 74.6% flagged among at-risk individuals versus 71.7% of controls, and 5–7% of converters versus about 1% of non-converters with temporal infranormal values. We will recompute it on identical z-maps. Beating it means a lower healthy flag rate at matched patient sensitivity.
The second baseline is a calibrated max-|Z| test. It uses the single most extreme vertex, ranked against the same calibration bank. This is the strongest simple competitor because it already has exact calibration and differs from ours only in ignoring spatial contiguity. It is the ablation that isolates our key ingredient.
The third baseline is a global mean-absolute-deviation score, calibrated the same way. It captures diffuse effects without localization.
The strongest existing supervised method is FAAE. It reports AUROC 68.56% and sensitivity 70.00% on OASIS-3 and sensitivity 72.20% on ADNI. We will rerun it on the same subjects, splits and covariates, with an equal hyperparameter search budget. Our score is unsupervised, so we compare AUROC and sensitivity at the 5% healthy false-positive rate. Matching FAAE's AUROC while adding calibration and localization counts as success. Exceeding it would be a bonus, not a requirement.
Finally, a linear-age ablation swaps the non-linear normative model for linear residualization and checks the age-binned false-positive rate.
Why not just…?
Why not just count infranormal regions with a stricter cutoff? A stricter cutoff lowers the healthy flag rate but still ignores spatial structure. Its false-positive rate is also not exact, because neighbouring regions are correlated. The Haas data show that region counts barely separate groups. The calibrated max-|Z| ablation is this alternative done properly, and the comparison between it and our cluster statistic is the decisive test of whether contiguity adds anything.
Why not just train a supervised classifier on deviation maps? This is a real threat on raw discrimination. Breaking the Norm reaches 77% balanced accuracy for severe depression when brain deviations are combined with polygenic risk scores. Supervised models, however, need labeled patients for each disorder. They produce scores without a guaranteed false-alarm rate, and they degrade when deployed. DEPLOYR measured one laboratory classifier dropping from AUROC 0.76 to 0.69 between retrospective testing and a prospective silent trial. If FAAE clearly beats us on AUROC, we will narrow the claim to calibration and localization, and we will report that outcome.
Why not just smooth the z-map and apply Bonferroni? Smoothing makes neighbouring tests more dependent, which makes Bonferroni even more conservative. Combrisson et al. document this power collapse for diffuse effects. We include this as a further comparison at matched false-positive rate.
Proposed Experiments
The first check is validity. On held-out healthy subjects from UK Biobank (adults) and dHCP term neonates (29–45 weeks post-menstrual age, using the developmental meshes of the ACDE work), the empirical flag rate must sit at the nominal 5% in every age bin. The same check under linear residualization should show inflation at the age extremes. In parallel, the partial correlation between $M_i$ and age, after spline adjustment for age, must be near zero.
The second check is discrimination and localization on ADNI and OASIS-3, comparing Alzheimer's patients with controls against all baselines. We expect significant clusters to concentrate in precuneus and prefrontal cortex, consistent with the regions FAAE highlights.
The third check, conditional on obtaining parcel-level ENIGMA data, runs the parcel-adjacency version of the test on the at-risk cohort. The question is whether calibrated coherent clusters reduce the 71.7% healthy flag rate to near 5% while preserving or enlarging the converter/non-converter gap. This is the most decisive test of the core claim, and a null result here would weaken it substantially.
The fourth check is a translation stress test. We calibrate on research scans and evaluate the healthy flag rate on SLIP-style clinical scans (Schabdach et al.). Their finding that segmentation software introduces more variance than cohort type predicts miscalibration when pipelines are mixed. We will measure it, and we will test whether a small local calibration bank of clinical controls restores the nominal false-positive rate.
References
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