Foundation models for brain signal arrived on the standard schedule. Large pretraining corpus, self-supervised objective, frozen encoder, linear probe, a table of clinical benchmarks with the pretrained row on top. LaBraM, EEGMamba, CBraMod, REVE, LEAD, BENDR and BIOT all exist, all report gains, and all are being proposed for clinical decoding.
Marzieh Zare ran the controls. The results are not a refutation of the approach, but they change what the published numbers mean.
What the controls found
The benchmark covers all seven models on five clinical tasks across four datasets. The primary analysis uses frozen linear probes with subject-disjoint leave-one-subject-out or grouped five-fold validation — the correct split, which is not universal in this literature. CAUEEG releases no patient identifiers, so it is evaluated at recording level with a patient-disjoint sensitivity analysis alongside, and the paper is explicit about that limitation rather than quiet about it.
Three findings matter.
On a matched 19-channel CAUEEG evaluation distinguishing Normal, MCI and Dementia across 1,187 recordings, classical features reach 0.734 macro-AUROC. BIOT reaches 0.699, CBraMod 0.669, REVE 0.568. The patient-disjoint sensitivity analysis retains the ordering — classical 0.717 against REVE’s 0.565. The handcrafted baseline wins, and it is not close for the weakest of the pretrained models.
A matched randomly-initialised encoder exceeds pretrained REVE on the same task, 0.659 against 0.570. Pretraining is not merely failing to help here; the pretrained weights are worse than no pretraining at matched architecture.
Dataset identity decodes from frozen REVE embeddings at or near ceiling across Western-Korean and Western-Western dataset pairs. That survives PCA to 50 dimensions and survives removal of line-frequency and amplitude-scale information — the two obvious confound channels. Zare is careful about what this licenses: it establishes dataset membership, not a causal site or population effect. But an embedding that encodes which dataset a recording came from, robustly, after the obvious nuisance variables have been stripped, is an embedding with a large and well-characterised shortcut available to any downstream probe.
Not every result runs one way. On CHB-MIT cross-subject ictal detection across 23 subjects, REVE reaches 0.793 against 0.739 for the best enhanced nonlinear comparator, 0.701 for random initialisation and 0.505 for raw-signal random features. The pretrained model wins. The paper still declines to overclaim, noting that because preprocessing removes absolute amplitude, this does not establish superiority over every plausible handcrafted baseline.
Why the conclusions move
The sentence to take from the paper is that conclusions change materially after montage matching, patient-overlap checks, stronger comparators and representation controls. Each of those four is cheap. None require new data collection. All four are routinely omitted.
The omissions compound in a specific direction. Montage mismatch inflates the pretrained model, which has seen many montages, against a classical pipeline tuned for one. Weak comparators inflate everything. Patient overlap inflates any model with enough capacity to memorise. Skipping representation controls means nobody checks whether the embedding has learned the task or learned the room. Zare distils the checks into a reporting protocol, which is the part that could actually change practice — a protocol is adoptable in a way that a critique is not.
The broader point is not confined to EEG. Any domain where a foundation model is trained across heterogeneous acquisition sites and evaluated on a clinical label that correlates with site has this failure mode. EEG is where it has now been measured.
What the alternative looks like
Three papers from the same fortnight suggest what brain models look like when the claim is scoped to something the evaluation can support.
Christopher Warner, Jonas Mago, JR Huml and Beren Millidge’s ZUNA1.1 is a 380M-parameter diffusion autoencoder aimed at reconstruction rather than clinical inference. It handles variable-length sequences up to 30 seconds with an arbitrary number of channels at arbitrary scalp locations, and reconstructs arbitrary temporal intervals within channels as well as entire channels. The comparator is spherical spline interpolation, which is ubiquitously deployed in MNE and is the thing practitioners actually use for bad-channel repair; ZUNA1.1 substantially outperforms it, and performs at least on par with the earlier ZUNA1 while being considerably more flexible. It is released under Apache 2.0.
Reconstruction quality is directly measurable against held-out ground truth. There is no label whose correlation with acquisition site can quietly do the work. That does not make the model more impressive than the clinical decoders; it makes the claim checkable.
Zijian Dong and colleagues’ NeuroWorld pushes in a different direction, forecasting how neural states evolve under continuous sensory input rather than mapping stimulus to response. The architecture separates endogenous neural state, from fMRI, from external multimodal stimuli, learns latent dynamics without reconstructing the fMRI signal, and then autoregressively rolls out brain states while maintaining strict causal access to stimuli. Evaluation spans three naturalistic movie-fMRI datasets and 30 participants, including a new Singapore Multimodal Imaging and Naturalistic Dataset with 8,519 paired stimulus-response clips and 140.7 person-hours of viewing.
The framing as a world model is doing real work. A world model is evaluated on forecast horizon, which degrades measurably and cannot be rescued by a shortcut in the label.
Interpretability as a control
The most instructive of the three is Ilia Semenkov, Daria Kleeva, Ivan Dakhtin, Zarina Maksudova and Alex Ossadtchi’s MEG speech-retrieval work, because it treats interpretability as a validation method rather than a presentation layer.
Short segments of perceived speech can already be retrieved from non-invasive MEG by deep networks trained with a CLIP-style objective against wav2vec 2.0 embeddings. The problem the authors identify is that the resulting weights do not map onto electrophysiological quantities, so nothing about the model tells you which speech properties drive retrieval or whether the retrieval is physiologically grounded at all.
The redesign is aimed at that. The spatial attention front end, which had operated on a flattened sensor layout, is replaced with spherical harmonics defined on the three-dimensional MEG helmet geometry. The subject-specific representation is reduced from 270 branches to 25, each with a temporal filter so it can be matched to a neuronal source in space and time. The convolutional decoder is made shallower. Ocular and cardiac components are removed before training, specifically to reduce the risk of stimulus-locked shortcuts — the same concern Zare raises, handled at the design stage.
On MEG-MASC the model reaches 39.75 ± 0.34% Top-1 accuracy among 1,005 candidates across six trained solutions, with roughly twenty times fewer decoder parameters. Because the weights map to source space, they recover generators consistent with the known speech-perception network, and left-lateralised branches carry higher-frequency rhythmic components not evident on the right.
The paired occlusion analysis is the part worth importing elsewhere. Fifteen of nineteen stimulus features contribute, with the largest effects for silence, sound intensity, vowels and acoustic onsets. Random word lists behave in the opposite direction: substituting narrative MEG into them improves retrieval, which says that activity without narrative structure carries less recoverable information than activity during coherent speech. And the wav2vec target can be reduced to about twelve learned feature dimensions with no accuracy loss, while strong temporal compression costs accuracy clearly — the information is in the timing, not the dimensionality.
Every one of those is a statement that could have come out false. A model that recovered no plausible generators, or where occlusion showed a single feature carrying everything, or where narrative substitution made no difference, would have been caught by its own analysis.
The protocol is the contribution
Zare’s paper will be read as a negative result about EEG foundation models. That reading is too narrow. The contribution is a reporting protocol — stronger classical comparators, label permutation, scrambled-label fine-tuning, random-initialisation controls, and a check on what the frozen embedding encodes about acquisition rather than about the patient.
Run against that protocol, the other three papers hold up for structural reasons rather than lucky ones. Reconstruction has ground truth. Forecasting has a horizon. Source-mapped weights and occlusion analyses are falsifiable by construction. Clinical classification across pooled multi-site corpora has none of those properties by default, which is why it needs the controls most and has received them least.