Some people control a motor-imagery brain-computer interface (BCI) well within minutes. Others, roughly 15 to 30 percent of users, never do. A motor-imagery BCI is a system that decodes imagined hand movements from scalp electroencephalography (EEG). The best-replicated way to predict who will succeed is to record a few minutes of EEG at rest and measure the strength of the sensorimotor rhythm (SMR), an 8–13 Hz oscillation over motor cortex that weakens when a person imagines moving. In an 85-person validation, this resting measure correlated with later BCI accuracy at ρ = 0.49 (Trocellier et al.). That result is usually read as saying that people with strong resting rhythms are neurally better equipped to modulate them. There is a more mundane reading. A decoder can only detect a drop in a rhythm that stands clearly above background noise at the scalp, and how clearly it stands out depends on skull thickness, electrode contact, leakage from occipital alpha, and the individual peak frequency. Under this reading, the resting rhythm predicts success because it makes the same imagined-movement effort easier to measure, not because the person modulates more.
We propose to separate these two explanations for each person with a counterfactual that needs no new hardware. For each subject, we take their own resting EEG, inject a synthetic, identical-for-everyone weakening of their sensorimotor rhythm into it, and run the exact decoding pipeline used on their real imagery trials. The resulting "detectability accuracy" answers one question: how well would this person score if their brain modulated exactly as much as everyone else's? We then invert the relation to recover a per-subject "modulation depth": the amount of rhythm suppression that, injected into their own rest data, reproduces their actual accuracy. This splits BCI aptitude into a measurement component and a modulation component. We then ask which of the two the famous resting predictors actually track, which one changes with training, and how much of the field's small-sample enthusiasm survives once the split is made.
Core Claim
Our central hypothesis is that most of the predictive power of resting spectral markers for motor-imagery BCI accuracy comes from how detectable a subject's rhythm is at the sensors, not from how strongly the subject modulates it. The residual modulation depth, estimated from the counterfactual, is the quantity that should be stable across sessions yet responsive to training.
If this holds, three consequences follow. First, screening tools based on resting rhythms are really measurement-quality tools. Second, "BCI illiteracy" splits into two different problems: some users are hard to see, and some users do not modulate. Third, interventions aimed at the modulation component, such as feedback training or the co-adaptive decoders of Blankertz et al., should help the second group and not the first.
The causal content of the claim is deliberately narrow. We do not infer brain-network causality. We run a controlled intervention on the measurement pathway, in silico, holding the modulation fixed. That is the one arm of the causal diagram we can manipulate exactly with existing data.
Where This Sits in the Literature
Three lines of work motivate the proposal by documenting the predictive gap without explaining it. Trocellier et al. is the closest existing work. It re-tested six literature predictors on 85 naive users and found that resting SMR power, variance of peak frequency, and number of spectral peaks replicated. The multi-band ratio PPfactor (p = 0.4959) and relative beta power did not. The study is purely correlational and does not ask what the surviving predictors measure; we take its dataset and its SMR-predictor as our primary target. Suk and Lee predicted accuracy from two minutes of rest at r = 0.581 on 80 subjects. Their method, Bayesian Spatio-Spectral Filter Optimization (BSSFO), learns spatial and frequency filters at 0.5 Hz resolution, and the study showed that individual peak frequencies vary widely. Our detectability model inherits that lesson: it injects modulation at each subject's own peak rather than in a fixed band. Rimbert et al. replaced rest with a physical probe, median nerve stimulation (a painless wrist pulse that evokes desynchronization over motor cortex), and reached ρ = −0.71 on 31 subjects and ρ = 0.61 out of sample. The same probe gave ρ = −0.87 on 20 subjects in their earlier study. That probe is itself a relative power drop at electrode C3, so we expect it to share the detectability confound. The shrinkage from 20 to 31 subjects is also the pattern that effect-size inflation predicts.
Two lines constrain the design. Mendes et al. document how underpowered brain–behavior studies inflate the effects that cross significance thresholds. With only about 80–110 subjects per dataset, this rules out fitting rich multivariate predictors and demands that our key quantities be low-dimensional and preregistered. Chevallier et al. show on MOABB, a benchmark of 36 public BCI datasets, that Riemannian tangent-space pipelines exceed 0.80 AUC in motor imagery while deep models sit at 0.60–0.70 and need more than 150 trials per class. We therefore use Riemannian and filter-bank pipelines as the decoders inside our counterfactual.
The causal framing borrows from, but differs from, three papers. Barmpas et al. cast decoding as anti-causal: intention causes brain state, which causes sensor signals. They use that framing to design a cross-subject network, and we use the same chain to define which arm we intervene on. Functional causal flow predicts microstimulation effects from resting spiking with R² up to 0.56, and INCAMA recovers directed graphs from EEG and fMRI after physics-aware inversion. Both infer causal structure inside the brain and were validated on anatomy or stimulation, never on behavior, and INCAMA only at population scale. We do not attempt whole-brain causal discovery at N ≈ 85. We intervene on something we can control exactly, the signal-to-noise path from rhythm to sensor.
Research Program
The counterfactual is built per subject $s$. We cut resting EEG into pseudo-trials matched in length and number to that subject's real imagery trials. At each subject's individual SMR peak, estimated after separating the periodic peak from the aperiodic 1/f background, we multiply the narrow-band rhythm component by $(1-\delta)$ over the hemisphere contralateral to a pseudo-label. Here $\delta$ is a fractional suppression, and the spatial spread follows a fixed lateralized sensorimotor pattern shared by all subjects. We run the same decoder, with the same cross-validation, that produces the subject's real accuracy $A_s$. This yields a curve $D_s(\delta)$, the detectability accuracy as a function of injected suppression. The per-subject modulation depth is then defined as
$$\hat\delta_s = \{\delta : D_s(\delta) = A_s\},$$
the suppression that, injected into this person's own rest data, reproduces their real accuracy. Detectability at a fixed reference suppression $\delta_0$ (for example the cohort median of $\hat\delta_s$) is written $D_s(\delta_0)$. $D_s(\delta_0)$ captures measurement quality with modulation held equal across people, and $\hat\delta_s$ captures modulation with measurement factored out.
Before trusting the split, we validate it in three ways. First, we inject each subject's empirically measured imagery-period power drop (expressed as a fraction) and check that $D_s$ reproduces $A_s$. If it does not, the injection model is missing something, such as spatial pattern differences or non-rhythmic imagery signals, and we report that failure as a result. Second, we run a null injection with $\delta = 0$ to confirm chance-level accuracy and catch leakage. Third, we ask whether $\hat\delta_s$ estimated from the first half of a session predicts accuracy in the second half better than raw accuracy does.
The frequency-band analysis enters in two ways. Detectability is computed in a fixed canonical 8–13 Hz band and at the individual peak. The gap between the two quantifies how much of "aptitude" is a band-definition artifact. Separately, we test whether the PPfactor's failure to replicate follows from its band ratios mixing periodic power with the aperiodic slope. If it does, a PPfactor computed on aperiodic-corrected power should behave like the SMR-predictor.
Baselines
The naive reference predicts every subject's accuracy as the training-fold mean. Any predictor must beat its leave-one-subject-out mean absolute error.
The main scientific competitor is the resting SMR-predictor exactly as re-implemented by Trocellier et al., with a reported Spearman ρ = 0.49 on the 85-subject Dreyer et al. (2023) dataset. We recompute it on the same subjects and the same accuracy definition. Our claim is not that $D_s(\delta_0)$ must predict better. The claim is that $D_s(\delta_0)$ should predict at least as well, and that the SMR-predictor's partial correlation with accuracy, controlling for $D_s(\delta_0)$, should fall below 0.15. If the partial correlation stays near 0.49, the hypothesis is wrong.
The strongest reported resting predictor is Suk and Lee's BSSFO-based model, r = 0.581 on the Berlin 80-subject cohort. That cohort may not be available to us, so we re-implement their spectral-prototype regression on our datasets under identical cross-validation. The strongest predictor of any kind is median nerve stimulation, with LOSO ρ = 0.61 and MAE = 9.0 on 31 subjects (Rimbert et al.). It uses data we do not hold, so we compare against that number only descriptively. We will request the recordings to test whether stimulation-evoked desynchronization is also partly explained by $D_s(\delta_0)$.
A multivariate competitor is ridge regression from each subject's resting tangent-space covariance features to accuracy, the Riemannian representation that Chevallier et al. show dominates decoding. We found no reported result on Lacuna for resting-covariance regression onto BCI accuracy. It will get the same nested tuning budget as every other predictor.
The ablations that isolate our key ingredient are three. The first uses fixed-band instead of individual-peak injection. The second skips aperiodic correction. The third replaces the subject's own rest data with a population-average spectrum while keeping their own trial counts. This last one removes everything subject-specific except trial count, and should destroy the detectability signal if the measurement explanation is right.
Why not just…?
Why not just keep using resting SMR power, since it already works? It does work, and it will likely stay about as predictive. Our question is what it measures, which changes what one should do with a low score: fix the measurement (montage, spatial filtering, peak-tuned bands) or train the user. The real threat is that $D_s(\delta_0)$ turns out to be nothing more than a noisier re-expression of SMR power. The partial-correlation test and the learning-slope test below distinguish "same number, better interpretation" from "no new information," and we will report the latter plainly if it occurs.
Why not just use median nerve stimulation, which explains far more variance? The ρ = −0.87 at N = 20 shrank to −0.71 at N = 31 (Rimbert et al., Rimbert et al.). That shrinkage is consistent with effect-size inflation in small samples. The probe also measures a relative power drop at one electrode, which is exactly what detectability governs. It needs stimulation hardware and was tested only in right-handed, eyes-closed, binary settings. Stimulation may still be the better screening tool. Our analysis predicts that some of its power is shared with $D_s(\delta_0)$, and applying the counterfactual to its data would test that directly.
Why not just fit a Riemannian or foundation model on resting EEG to predict accuracy? With 54–109 subjects per dataset, a high-dimensional predictor of one number per person is exactly the regime where Mendes et al. warn of spurious, inflated findings. Even a well-validated black-box predictor would not say whether it tracks measurement or modulation. We include the tangent-space ridge baseline so that its performance is on the record rather than argued away.
Why not just infer resting causal networks with functional causal flow or INCAMA? Those methods target brain-internal directed influence and have been validated on spiking arrays, simulations, or more than 1,000 fMRI subjects (FCF; INCAMA). Neither has been characterized at N ≈ 85 scalp EEG or linked to behavior. Even if they worked, they would not address the more basic confound that the decoder's visibility of the rhythm varies across heads. Our intervention is narrower but exactly controlled.
Why not just do a real intervention, such as rhythm-targeted brain stimulation? Ultimately that is the right test of the modulation arm, and theta stimulation work such as dual-brain tACS shows stimulation can shift behavior. Our split tells such a study whom to target. Stimulating low-detectability users would be expected to fail under our hypothesis, and that is a sharp, preregistrable prediction for a follow-up.
Proposed Experiments
The primary analysis uses the Dreyer et al. (2023) 85-subject dataset with its resting baselines and binary left/right imagery. The confirmatory replication uses the 109-subject PhysioNet dataset: its eyes-open and eyes-closed baseline runs supply rest, and we follow Barmpas et al. in the exclusions that leave 103 usable subjects. Lee2019 and Stieger2021, downloadable through MOABB via the TSMNet codebase, supply multi-session data where resting or pre-trial baseline segments exist. Stieger2021's repeated training sessions are what make the learning test possible.
Actual accuracy $A_s$ is computed with two decoders, filter-bank common spatial patterns (Ang et al.) and tangent-space logistic regression. All conclusions must hold for both. We preregister three primary quantities before touching the replication set: the partial correlation of the SMR-predictor with $A_s$ given $D_s(\delta_0)$, the correlation of $\hat\delta_s$ with the SMR-predictor, and the correlation of each component with learning slope.
The first decisive check is the partial correlation described above, in both the discovery and replication cohorts. The second is the learning dissociation. On Stieger2021, we predict that first-session $D_s(\delta_0)$ explains first-session accuracy but not improvement across sessions, whereas $\hat\delta_s$ rises with training. We also predict that $D_s(\delta_0)$ is more stable across sessions than $\hat\delta_s$. The third check is a sample-size study. We repeatedly subsample cohorts of 10 to 80 subjects and plot the distribution of observed correlations for the SMR-predictor, number of peaks, PPfactor (raw and aperiodic-corrected), $D_s(\delta_0)$, and $\hat\delta_s$. This shows at what N each predictor's significant findings stop being inflated. It also tests whether the small-cohort literature values, including the stimulation-probe correlations, fall where inflation would put them.
The hypothesis is refuted under any of three outcomes. First, if the SMR-predictor keeps most of its correlation after controlling for detectability. Second, if injecting each subject's measured imagery power drop fails to reproduce their accuracy. Third, if $\hat\delta_s$ carries no information about learning beyond raw accuracy. Any of these outcomes is publishable, because each settles what resting predictors of BCI skill measure.
References
- VALIDATING NEUROPHYSIOLOGICAL PREDICTORS OF BCI PERFORMANCE ON A LARGE OPEN SOURCE DATASET
- The Berlin Brain–Computer Interface: Non-Medical Uses of BCI Technology
- Predicting BCI Subject Performance Using Probabilistic Spatio-Temporal Filters
- Reliable predictor of BCI motor imagery performance using median nerve stimulation
- Prediction of Motor-Imagery-BCI performance using Median Nerve Stimulation
- A functional connectome phenotyping dataset including cognitive state and personality measures
- The largest EEG-based BCI reproducibility study for open science: the MOABB benchmark
- A CAUSAL VIEWPOINT ON MOTOR-IMAGERY BRAINWAVE DECODING
- Predicting perturbation effects from resting activity using functional causal flow
- Recovering Whole-Brain Causal Connectivity under Indirect Observation with Applications to Human EEG and fMRI
- Theta Dual-Brain Stimulation of rTPJ Shapes Joint Agency
- Filter Bank Common Spatial Pattern Algorithm on BCI Competition IV Datasets 2a and 2b