Physically Anchored Label Noise for Tau PET Diagnosis

When several doctors look at the same brain scan and reach different diagnoses, machine learning usually treats the disagreement as random noise and averages it away. In dementia imaging this is the wrong move, because the disagreement is structured by chemistry. PET scans for tau — a protein that clumps into toxic filaments in several brain diseases — use radioactive tracers that bind only to particular three-dimensional filament shapes: postmortem tissue studies show that all three leading tau tracers bind Alzheimer's-type paired helical filaments and are chemically blind to the straight filaments of other tauopathies, and that the three tracers compete for the very same physical pockets (Head-to-head comparison of [18F]-Flortaucipir, [18F]-MK-6240 and [18F]-PI-2620 postmortem binding; Head-to-head comparison of [18F]-Flortaucipir, [18F]-MK-6240 and [18F]-PI-2620 postmortem binding across the spectrum of neurodegenerative diseases). So when a clinician reads a faint signal in a patient who actually has a non-Alzheimer's tauopathy, the error is not a random slip — it is the predictable consequence of a tracer that cannot see the patient's filament conformation. Meanwhile, the field's "gold standard" for validating these tracers, the postmortem neuropathological examination, is itself performed by humans who disagree with each other at rates comparable to any other specialty (Variability Matters).

This proposal builds a diagnosis model for tau PET that places a small set of physically verified cases — postmortem tissue with autoradiography (applying the radioactive tracer directly to tissue slices and imaging where it sticks) and immunohistochemical staining — at the center of the label-noise problem. The core insight is a symmetry that current methods cannot break: if every expert agrees, existing multi-rater models cannot tell whether the experts are all correct or all sharing the same blind spot. A handful of cases where the true filament conformation is chemically established breaks that symmetry, and lets the model learn, rather than assume, when consensus equals truth.

Core Claim

Diagnostic labels in tauopathy imaging are systematically noisy in a way determined by the mismatch between tracer binding geometry and the patient's fibril conformation, and this structure can be recovered — not just tolerated — by a latent-variable model whose latent disease type is pinned down on a small anchor set of chemically validated postmortem cases. Existing label-noise methods fail precisely here: per-sample trust approaches such as LiNC explicitly break when noise is systematic, because a panel consistently mislabeling one disease looks "clean" to the model (LiNC: Lightweight Noise Correction via Per-Sample Trust and Gaussian Mixture Modeling). Multi-rater generative models such as the Latent Doctor Model capture disagreement distributions but have no mechanism to distinguish shared expert error from shared expert accuracy (The Latent Doctor Model for Modeling Inter-Observer Variability), and the strongest panel-ensemble method to date likewise treats the human raters as the final authority (More is more). We claim that anchoring is the missing ingredient, and that it is testable on existing benchmarks plus one decisive new data design.

Research Program

The model has three components. Let $c_i$ be the true conformational subtype of case $i$ (Alzheimer's-type paired helical filaments, 4-repeat straight filaments of progressive supranuclear palsy or corticobasal degeneration, Pick's disease folds, TDP-43 pathology, or none), $x_i$ the in vivo PET measurement (regional uptake values and W-score maps), and $r_{im}$ the diagnosis given by reader $m$. We posit

$$p(c_i,\, x_i,\, r_{i,1:M}) \;=\; p(c_i)\, p(x_i \mid c_i)\, \prod_{m=1}^{M} p(r_{im} \mid c_i,\, x_i),$$

where $c_i$ is latent for ordinary cases and observed for cases in an anchor set $\mathcal{A}$ assembled from postmortem cohorts. The reader term is conditioned on the image, following Chatelain's finding that annotator reliability varies with image content rather than being a fixed per-annotator constant (Pierre Chatelain et al.); this lets the model represent, for example, that all readers tend to call faint globus pallidus signal "atypical Alzheimer's." Training maximizes the marginal likelihood, which is identifiable only because the anchors fix the $c$-to-reader mapping on known cases.

Crucially, we do not treat the anchor labels as perfect. Neuropathologists disagree too, and Braak staging already suffers documented disagreement over anatomical boundaries (The Use of Tau PET to Stage Alzheimer Disease According to the Braak Staging Framework). Anchor cases therefore carry two independent readouts: the physical assay pair of autoradiography plus multi-marker immunohistochemistry, exactly the co-staining protocol validated across 45 disease-spectrum cases in the head-to-head tracer study (Head-to-head comparison; the same protocol in 43 cases in Autoradiography validation of novel tau PET tracer [F-18]-MK-6240), and a neuropathologist panel whose labels enter the same likelihood as any other reader, merely with a learned high-precision profile. This directly answers the "silver standard" critique raised inside histopathology itself: Wilm and colleagues showed individual pathologists agree with panel consensus at F1 scores as low as 0.64 and explicitly called for biological markers to replace majority-vote truth (Influence of Inter-Annotator Variability on Automatic Mitotic Figure Assessment). Our design imports that lesson into molecular imaging validation, where it has never been applied.

The second component is a simulation engine for structured noise on real tau PET data. Using the ADNI and A4 tau PET data already used by TauAD for template learning (TauAD) and the clinical cohort of 65 patients and 23 controls scanned with PI-2620 (PI-2620 Binding Patterns), we inject reader labels whose confusion structure is calibrated to documented clinicopathological mismatch: Alzheimer's-type reads applied to 4-repeat tauopathies, faint off-target basal ganglia signal read as specific binding, and so on, on top of ordinary idiosyncratic noise. This gives controlled ground truth for the systematic-noise regime that no existing benchmark provides.

The third component is a paired-cohort data design for the field's most stubborn contradiction. Postmortem autoradiography finds zero specific PI-2620 binding to 4-repeat tau in PSP tissue (Head-to-head comparison), yet in vivo the same tracer discriminates PSP-Richardson syndrome from controls at AUC 0.77–0.81, with globus pallidus uptake tracking symptom severity at $\rho = 0.53$ (PI-2620 Binding Patterns). The anchored model can adjudicate the two candidate explanations: if the in vivo signal is genuine low-affinity binding that tissue washing destroys, anchored 4-repeat cases should show PET signal that correlates with symptoms despite negative autoradiography; if it is off-target neuromelanin accumulation (off-target binding documented in both postmortem studies), it should dissociate from tau staining burden. The same design addresses the cryo-EM paradox, where flortaucipir shows 1:1 stoichiometric binding to CTE Type I filaments but no detectable density on Alzheimer's filaments, presumably because low-occupancy binding is averaged away (Cryo-EM Structures of Chronic Traumatic Encephalopathy Tau Filaments with PET Ligand Flortaucipir; multiple binding sites resolved for a second ligand in Cryo-EM structures of tau filaments from Alzheimer's disease with PET ligand APN-1607): region-level occupancy estimated from the anchored model is exactly the quantity cryo-EM cannot see.

Baselines

The naive reference point is a deterministic classifier trained with cross-entropy on whatever single set of labels is at hand — the default in nearly all diagnostic machine learning, and the setting in which the failure modes we target first appear. On the closest studied analog, RetinaNet mitotic-figure models trained on single pathologists capped at F1 0.74–0.76 against panel consensus (Wilm et al.); no reported result found on Lacuna for this baseline on tau PET specifically. The consensus baseline replaces single labels with a three-expert majority vote before training, which Wilm shows slashes model variance (interquartile range of performance falling from 0.038 to 0.016) with little gain beyond three raters; we run it with the same readers our model sees.

The strongest existing competitor is Grove's Full Panel: one attention-based model per rater, combined into a panel distribution, which on the Dutch Esophageal Pathology Panel dataset reached average F1 78.2% and expected calibration error 0.050, versus 72.9% and 0.183 for the consensus model (More is more). It is the strongest because it, like us, preserves the full rater distribution rather than compressing it, and it holds the best reported calibration on a real multi-rater histopathology benchmark. We reimplement it on our tasks with the same backbone, identical training data, cross-validation splits, and tuning budget (equal random-search iterations for all methods), so any difference is attributable to anchoring. For distribution quality we also compare against the Conditional Latent Doctor Model, which achieved KL divergence 0.461 on Gleason2019 and entropy correlation up to Spearman 0.728 on ISUP (The Latent Doctor Model), and for noise correction against LiNC, which lifted mean last-epoch accuracy from 58.82% to 80.23% at 50% synthetic noise and reached noise-detection AUC 0.9837 on OrganSMNIST at 20% noise (LiNC).

Beating these means: on real multi-rater benchmarks, lower KL than 0.461 on Gleason2019 and higher entropy correlation than 0.728 on ISUP; on DEPP, average F1 above 78.2% with expected calibration error below 0.050, with the sharpest test being the cases Grove excluded as "indefinite for dysplasia," which our model must ingest rather than discard. On the structured-noise simulation, recovering the injected true subtype distribution where consensus and LiNC fail, measured by KL to the true label distribution and by downstream AUC. The key ablation is our own model with the anchor set removed, which reduces it to a Latent-Doctor-style model and isolates exactly what the physical anchors contribute; a second ablation sweeps anchor-set size from zero upward to find how few chemically verified cases are needed.

Why not just…?

Why not just take a majority vote of three experts? For random disagreement this works well: three-rater consensus cut performance variance dramatically in Wilm's study, and even the three least agreeable pathologists matched the most agreeable ones (F1 0.756 versus 0.751) (Wilm et al.). But majority vote is precisely the mechanism that fails under systematic noise — a panel sharing one blind spot votes confidently for the wrong answer, and Grove shows consensus-trained models are badly calibrated exactly where raters cluster (ECE 0.183 versus 0.050) (More is more). Our Experiment 1 injects shared bias on top of random noise and measures the crossover point where consensus stops working; if injected noise is mostly random, consensus will match us, and we will say so.

Why not just filter out low-agreement annotators? Subsetting by conformity demonstrably helps: models trained on the top-conformity pathologists beat models trained on everyone, while saving over a thousand annotation hours (Variability Matters). But conformity is measured against an anchor rater, not against tissue, so it filters idiosyncratic noise while preserving whatever the whole panel — anchor rater included — gets wrong. And there is a performance ceiling that annotator selection cannot bypass: single-annotator models capped at F1 0.74–0.76 regardless of whether the annotator's own agreement was 0.64 or 0.85 (Wilm et al.). Our ablation replaces star-annotator selection with physical anchoring on the same data, which settles directly whether chemical anchors buy what conformity filtering cannot.

Why not just use off-the-shelf noise correction like LiNC? LiNC's authors themselves flag the failure mode this proposal targets: its Gaussian-mixture trust clustering treats a consistently mislabeled group as clean, because the error is systematic rather than per-sample (LiNC). On purely symmetric flips, LiNC is excellent (80.23% mean accuracy at 50% noise) and may well beat us; we concede that regime. The decisive comparison is Experiment 1's systematic-noise arm, where we predict LiNC's detection AUC collapses toward the AUM/VoG range (0.8652/0.9126 on OrganSMNIST) while anchoring holds up, because anchors supply group-level information that per-sample margins cannot. Diffusion-based denoising such as DiN (DiN) addresses semantic noise but likewise contains no mechanism that ties the noise to a physical cause.

Why not just wait for better tracers? The chemistry argument fails on the evidence: the head-to-head study proved that first- and second-generation tracers occupy the same binding sites, mutually displace one another, and are uniformly blind to non-Alzheimer's conformations (Head-to-head comparison), and clinically PI-2620 still leaves roughly half of PSP patients without binding above control range (PI-2620 Binding Patterns). Better radiochemistry narrows random error; it cannot fix a labeling process that systematically misreads the conformations no tracer sees. The proposal is complementary to, not a substitute for, ligand development.

Experiments and Decisive Checks

Experiment 1 runs the structured-noise simulation on tau PET features (extracted with the diffusion-based anomaly setup of TauAD on ADNI/A4, applied to the PI-2620 clinical cohort of Blazhenets et al.), sweeping the ratio of systematic to random noise and the anchor-set size, and comparing against every baseline above under matched compute. Experiment 2 runs the real multi-rater benchmarks — Gleason2019, ISUP Grading, and DEPP including its indefinite-for-dysplasia cases — in both anchor-free mode (testing that we lose nothing where no anchors exist) and pseudo-anchor mode where unanimously agreed cases stand in for physical ones; the reported numbers to beat are KL 0.461, Spearman 0.728, and F1 78.2% at ECE 0.050 respectively. These benchmarks have no chemical ground truth, so here anchors are imperfect by construction — an honest stress test of how the method degrades as anchor quality falls.

The decisive check is the paired cohort: subjects scanned in vivo with a tau tracer during life, then examined postmortem with the autoradiography-plus-multi-stain protocol of the ADRC studies and a three-or-more neuropathologist panel, with reader-level agreement reported openly (inter-annotator agreement as low as Fleiss' kappa 0.43 in analogous large-panel settings warns against assuming a single true read, Variability Matters). Existing postmortem cohorts number in the forties (Head-to-head comparison), so this is a designed, ethically pre-registered accumulation rather than a retrospective mining exercise, in the spirit of the biopsy-verified Xiangya-Derm database, where histopathology rather than visual consensus anchored 150,000 clinical images and the resulting classifier beat 31 dermatologists (top-3 accuracy 84.77% versus 78.15%) (Xiangya-Derm). On that cohort, the model must adjudicate the in vivo versus postmortem PSP paradox with a pre-specified decision rule: symptom-correlated signal on chemically confirmed 4-repeat cases with negative autoradiography supports washable low-affinity binding; signal tracking neuromelanin-rich regions independent of tau staining supports off-target accumulation. Either outcome converts a standing contradiction in the literature into a measured parameter of the diagnostic model — which is, in the end, the point of treating physical evidence as an anchor for human disagreement rather than as its unquestioned replacement.