A major flaw in the paper resides in its strongest negative result, the diffusion “upper bound”. The paper calls this prior “provably optimal” and an upper bound, but the closed form it uses is only optimal over a fixed reference set, and here that set only contains training responses, while the test images are new. In practice the prior pulls the EEG of a new image toward the responses to other images, so it behaves like a nearest-neighbour average and cannot know anything about the test image. The paper’s own Table 11 shows this pretty clearly: with a full denoising step, accuracy is at chance for every noise level, and the best setting is the one that keeps 90% of the raw input.
Because of this, the “cannot” in the title rests on a prior that is built to fail on new images, which doesn't say much about priors in general. I would recommend renaming it (e.g., a nearest-neighbour denoiser), adding a learned diffusion prior trained on the training responses and tested on held-out images, and scoping the title and abstract to the methods that were actually tested.
A second major issue is that the EEG-side evidence for the mechanism has a few measurement confounds. First, the Wiener filter and the “full” learned denoisers only work in the top 512 of about 15,750 PCA dimensions and throw the rest away (this is visible in the supplementary code), while the plain average keeps everything. The projection alone already drops accuracy from 0.156 to 0.115, which is exactly what the “full” linear denoiser scores, so it isn't the denoiser itself that fails. Second, everything is read through a frozen encoder that is sensitive to any change in its input: even shrinking the true 80-repetition response drops accuracy from 0.841 to 0.247. So an accuracy drop cannot separate lost information from input that just looks unfamiliar. Third, Table 4 does not really show “anti-alignment”, since the top 512 directions keep about 68% of the accuracy and only the first ~32 are uninformative. Finally, the “signal energy” estimate assumes the noise is uncorrelated across features, which is not true for EEG, so the top variance directions might be mostly noise to begin with.
This matters because the mechanism is the main new contribution of the paper and gives it its title. The main gap in Table 1 is not affected, but its explanation is. I would recommend refitting the denoisers at full rank (or cleaning only the top subspace and keeping the rest), training a fresh linear decoder on each modified input, and ordering directions by signal-to-noise, with a noise covariance estimated from the repetitions, instead of by variance.
Other minor points: the text says no classical estimator beats the plain mean, but Table 12 shows two that do (by tiny margins). The EEG row of Table 10 uses medians while the text uses means, which creates an apparent outlier (8.1%) that disappears with means. The Table 13 caption says the “golden” rows shrink toward the origin, but the code shrinks them toward the average training response. The “canonical-correlation basis” is in fact a PCA basis, since no CCA is computed. There are also some factual slips: NeuroBridge reports 63.2% (not 62.3%), THINGS-MEG has 272 gradiometers (not 271 magnetometers), and appendix sections B and E are empty.