Patients who share a psychiatric diagnosis often have brain rhythms that differ more from one another than healthy people's do. In autism, resting alpha peak frequency and amplitude show no group-average difference from controls, yet they show significantly inflated spread across children (Lefebvre et al.). That spread is usually read as biological heterogeneity: hidden subtypes waiting to be separated. There is a more boring explanation, and nobody has ruled it out. Clinical EEG recordings are short and full of artifacts, and patient groups tend to give shorter, noisier clean segments than controls. A per-person peak frequency estimated from less data is simply less precise, and that imprecision shows up as extra between-person variance. The same study found that rerunning the analysis in different software changed which effects were significant, which is what you would expect if per-person estimates sit close to their noise floor.
We propose to separate the two explanations. We fit each person's EEG with an autoregressive model, which treats the signal as white noise passed through a resonant filter. A brain rhythm then becomes a pole of that filter: a complex number whose angle gives the rhythm's center frequency and whose distance from the unit circle gives how sharply tuned it is. Autoregressive theory gives an analytic standard error for each pole from a single short recording. That lets a hierarchical model subtract each person's measurement noise before asking two questions: is a group really more variable than controls, and is the extra variation continuous spread or discrete subtypes? The parametric estimator serves as a measuring instrument with known error bars, not as a source of extra features for a classifier.
Core Claim
Variance inflation and data-driven "biotypes" in resting EEG cannot be interpreted until each subject's own estimation error is removed. Pole-based autoregressive models make that removal possible on records too short to bootstrap reliably. Write $\hat\theta_i$ for subject $i$'s estimated alpha pole (center frequency and bandwidth), $s_i^2$ for its analytic sampling variance, and $\theta_i$ for the true value. We model
$$\hat\theta_i = \theta_i + e_i,\quad e_i \sim \mathcal{N}(0, s_i^2),\qquad \theta_i \sim \sum_{k=1}^{K} \pi_{k,g}\,\mathcal{N}(\mu_{k,g}(\text{age}), \tau_{k,g}^2),$$
where $g$ is the diagnostic group, $K$ is the number of latent subtypes, $\pi_{k,g}$ are subtype proportions, $\mu_{k,g}$ are age-dependent subtype means, and $\tau_{k,g}^2$ are true between-person variances. The sampling variance $s_i^2$ comes from the standard large-sample result that autoregressive coefficient estimates have covariance of about $\sigma^2 R^{-1}/N$. Here $\sigma^2$ is the driving-noise variance, $R$ the autocorrelation matrix and $N$ the number of clean samples. We map that covariance to the pole through the derivative of a polynomial root with respect to its coefficients, then inflate it by averaging across candidate model orders. Order averaging addresses the known failure in which one extra order creates a spurious peak (Zhao and Gui).
The claim is falsifiable in both directions. ASD or MDD variance inflation may survive deconvolution, in which case it is real. It may vanish, in which case it was largely a data-quality artifact. Separately, a $K=2$ or $K=3$ mixture may or may not beat a single inflated Gaussian once noise is accounted for.
Research Program
The work has three parts. First, an estimator. We use Burg autoregressive fitting on artifact-cleaned contiguous segments. Burg is chosen because it is stable on short records and gave sharper peaks than Yule-Walker and maximum-likelihood fitting (Zhao and Gui), and because it beat both Welch and subspace methods as an EEG spectral front end (Ding et al.). We fit orders in a window around the information-criterion choice and weight them by that criterion. We extract the dominant pole in 6–14 Hz together with its delta-method covariance. Prior clinical uses of autoregressive models integrated the spectrum back into five fixed bands and discarded the poles: the coma versus brain-death classifier of Zhu et al. did this, as did the ketamine-response work of Wu et al., which used band power directly. We keep the pole and its uncertainty.
Second, the measurement-error mixture model above. We fit it with Bayesian inference and compare $K$ by held-out likelihood and a parametric bootstrap test of $K=1$ against $K=2$. Normative age effects $\mu(\text{age})$ are smooth splines, which mirrors the normative-modeling logic of Lefebvre et al. but adds the noise term their LOESS approach lacked.
Third, a reproducibility harness. The full pipeline runs in Python (MNE plus a reference Burg implementation) and in an independent Matlab implementation, so we can test whether defining the peak as a polynomial root removes the software divergence that peak-picking showed. Gap 3 in the file raises this question as untested.
Data come from the public MODMA 128-channel resting EEG (24 MDD, 29 controls; MODMA) and from the Mumtaz (58 participants) and Rest (121 participants) depression datasets used in the fairness study. Together these give three independent replications of an MDD heterogeneity estimate. We will request the PARIS ASD cohort analyzed by Lefebvre et al. and the Taipei ketamine cohort of Wu et al.; the claims that depend on them are marked as conditional. Every real-data analysis is preceded by simulations with known $\tau^2$, known $K$, and record lengths drawn from the empirical clean-segment-length distributions of each dataset.
Baselines
The naive reference is the analysis the field already does: per-subject alpha peak frequency from a Welch periodogram with peak-picking, a raw comparison of group variances (Levene's test), and k-means on band powers. This is the procedure whose conclusions we suspect are confounded by data quality. Beating it means showing that it reports variance inflation or clusters in simulations where none exist, at the record lengths seen in practice, while our model does not.
The strongest existing method for the heterogeneity question is LOESS normative modeling of alpha peak frequency and amplitude as in Lefebvre et al.. It reports significant ASD variance inflation at p < 0.05 but gives no effect size, so beyond that p-value there is no reported result found on Lacuna for a variance-ratio estimate. We rerun it on identical cleaned segments with the same age covariate. On simulations, the comparison is calibration of the variance-inflation test (false positive rate at nominal 5%) and power at a fixed true $\tau^2$ ratio. On real data, the comparison is whether conclusions agree across the three depression datasets.
For downstream validity the strongest competitor is the supervised band-power model of Wu et al.. Its baseline relative theta and low-alpha powers with an RBF support vector machine reached 81.3 ± 9.5% accuracy for ketamine response. If that cohort is obtained, beating it means that adding deconvolved subtype membership improves cross-validated accuracy under the same folds and the same tuning budget. For diagnosis on MODMA, the reference is the 82.31% accuracy of logistic regression with ReliefF on combined features (Sun et al.). Our aim is not to beat that number. We will report whether pole features plus uncertainty weighting match it, as a sanity check that the poles carry signal.
Two ablations isolate the key ingredients. The first keeps Burg poles but sets $s_i^2 = 0$, which isolates deconvolution. The second keeps deconvolution but replaces analytic $s_i^2$ with an epoch-bootstrap variance from multitaper peak estimates, which isolates the parametric estimator.
Why not just…?
Why not just use multitaper spectra and bootstrap over epochs to get per-subject uncertainty? This is the most serious threat, and the second ablation tests it directly. Bootstrapping needs many independent clean epochs. The settings where heterogeneity matters most are pediatric autism, ICU coma recordings of about one minute (Zhu et al.), and four-channel wearable EEG. These often yield only a few. Non-parametric smoothing also trades resolution for variance in a way that blurs nearby peaks (Zhao and Gui). We expect the analytic route to win below roughly 30 s of clean data and to tie above it. If it ties everywhere, we will report that the deconvolution, not the estimator, is the contribution, and recommend multitaper plus bootstrap.
Why not just cluster band powers or deep EEG embeddings? Clustering finds clusters whether or not they exist. Without per-subject error bars, a noisier subgroup appears as a separate "biotype." This is the same post-hoc fragility flagged for small biotyping studies such as Lee et al. (n = 60). Large autoregressive EEG foundation models such as THD-BAR give embeddings with no notion of measurement precision. End-to-end depression models on these same datasets also carried demographic biases that resisted mitigation (fairness study). We include embedding-plus-GMM as a comparison in the simulation, where the true $K$ is known.
Why not just stratify by clinical severity scores? Severity scales cut across physiological endotypes in brain injury (Holst et al.), and questionnaire totals are noisy proxies for latent state (Chen et al.). We nonetheless test it: if deconvolved subtype membership is fully explained by severity score where available (MODMA scales), the EEG subtypes add nothing.
Proposed Experiments
The first decisive check is simulation calibration. Across record lengths of 10–120 s, at signal-to-noise levels matched to each dataset, with true group variance ratios from 1.0 to 2.0 and true $K \in \{1,2,3\}$, we compare the naive pipeline, LOESS normative modeling, and our model. The naive pipeline should show inflated false positives whenever groups differ in clean-data length, and ours should stay near nominal. We also measure whether the analytic $s_i^2$ matches empirical error, using split-half reliability within each real recording. This tests the theory directly, since the order-averaged variance should cover the split-half discrepancy about 95% of the time at the 95% level.
The second check applies the method to MDD heterogeneity in MODMA, Mumtaz, and Rest. We report deconvolved variance ratios with intervals and the posterior over $K$, and ask whether the three datasets agree. An inflation that survives deconvolution and replicates in all three is real. One that disappears in all three was data quality.
The third check is the software test. We compare between-implementation agreement of per-subject peak frequency (intraclass correlation) for root-based poles against Welch peak-picking, and check whether group-level conclusions flip between implementations.
The conditional extensions use the PARIS cohort to rerun the exact Lefebvre et al. contrast with deconvolution, and the Taipei cohort to test whether subtypes add to the 81.3% band-power response baseline. If the ASD inflation collapses once clean-segment length is modeled, that result alone changes how alpha "heterogeneity" findings should be read.
References
- Alpha Waves as a Neuromarker of Autism Spectrum Disorder: The Challenge of Reproducibility and Heterogeneity
- Nonparametric and parametric methods of spectral analysis
- On the Utility of Power Spectral Techniques With Feature Selection Techniques for Effective Mental Task Classification in Noninvasive BCI
- A Hybrid System for Distinguishing between Brain Death and Coma Using Diverse EEG Features
- Identifying Ketamine Responses in Treatment-Resistant Depression Using a Wearable Forehead EEG
- MODMA dataset: a Multi-modal Open Dataset for Mental-disorder Analysis
- Machine Learning Fairness for Depression Detection Using EEG Data
- A study of resting-state EEG biomarkers for depression recognition
- Peripheral inflammatory biomarkers define biotypes of bipolar depression
- THD-BAR: Topology Hierarchical Derived Brain Autoregressive Modeling for EEG Generic Representations
- Clustering identifies endotypes of traumatic brain injury in an intensive care cohort: a CENTER-TBI study
- Representation Learning for Integrating Multi-domain Outcomes to Optimize Individualized Treatment