When the same magnetic pulse is delivered to the same spot of a person's motor cortex, the muscle twitch it produces can be large on one trial and nearly absent on the next. This trial-to-trial variability is the main obstacle to using transcranial magnetic stimulation (TMS, a coil that induces a brief current in the cortex) as a reliable readout of how excitable a brain circuit is. The standard explanation looks at a single scalp electrode and asks whether the local 8–14 Hz sensorimotor "μ rhythm" was strong, or at a particular point in its cycle, when the pulse arrived. Results disagree, and the electrode may be picking up the wrong brain area. We propose a different explanation that can still be tested in small samples. Excitability on a given trial depends on how tightly the sensorimotor network is phase-synchronized in the half-second before the pulse. That synchrony can be summarized by one number, the largest eigenvalue (spectral radius) of the moment-to-moment synchrony graph among sensorimotor electrodes.
The opportunity comes from three pieces of evidence that are each in place but have never been joined. Biophysical modeling shows that the coupling strength at which a connectome tips into global excitation tracks the network's spectral radius. Closed-loop TMS work shows that single-channel oscillatory markers are inconsistent. Small-cohort clinical work shows that a few well-chosen scalars beat high-dimensional feature sets. The contribution is a pre-registered, small-sample-valid test of whether one graph-derived scalar explains motor evoked potential (MEP, the muscle response recorded by electromyography) variance beyond μ power and phase, and whether that effect grows at weak stimulation intensities as theory predicts.
Core Claim
Let $A_t$ be the matrix of pairwise μ-band phase-locking values among roughly eight to twelve electrodes over bilateral sensorimotor cortex. Each entry is computed in a fixed window ending at the moment of pulse $t$, after a surface Laplacian has reduced volume conduction. Let $\lambda_t$ be its largest eigenvalue. The motivating intuition comes from linearized coupled-population models. In a system $\dot{x} = -x + cWx$, where $x$ is population activity, $W$ the coupling graph and $c$ a global gain, the quiet state destabilizes when $c\,\lambda_{\max}(W) > 1$. A larger spectral radius therefore means less additional drive is needed to push the network over threshold. Global excitability and network structure in the human brain showed exactly this relationship on static diffusion-MRI connectomes in Wilson-Cowan simulations, where the transition threshold correlated with spectral radius ($r^2 = 0.885$). Our claim transfers that structural result to fast functional graphs in living subjects. We predict, before seeing data, that higher pre-stimulus $\lambda_t$ yields larger MEPs after controlling for local μ power and phase. We further predict that this effect is proportionally strongest at low stimulation intensities, where the input-output curve has not saturated.
The test is the trial-level mixed model
$$\log \mathrm{MEP}_{it} = \beta_{0i} + \beta_1 \lambda_{it} + \beta_2 P_{it} + \beta_3 \cos\phi_{it} + \beta_4 \sin\phi_{it} + \beta_5\, \lambda_{it} I_{it} + \varepsilon_{it},$$
where $i$ indexes subjects with their own intercept $\beta_{0i}$, $P$ and $\phi$ are pre-stimulus μ power and phase at the target electrode, and $I$ is stimulation intensity relative to the subject's input-output curve. The claim stands if $\beta_1 > 0$ and $\beta_5 < 0$ under subject-level cross-validation.
Why This Is Not Already Done
The closest work splits into two camps that do not touch.
Closed-loop TMS studies treat the brain state as one channel. The Association of EEG μ Rhythm Phase and Power with TMS-Assessed Cortical Excitability States used an individualized LSTM to time pulses to μ phase at C3 in 30 subjects at 120% of resting motor threshold. It found that power, but not phase, related to MEP size, and it flagged that C3 may reflect sensory rather than motor cortex. EEG-triggered TMS reveals stronger brain state-dependent modulation of motor evoked potentials at weaker stimulation intensities found significant phase modulation in 15 subjects. Its key observation was that detection depends on intensity: the null was rejected in 62% of cases at the lowest intensity versus about 35% at the highest. That observation largely reconciles the two papers, and it shapes our design, since we sample several intensities rather than one saturating level.
Dynamic-network studies, by contrast, do not measure excitability. Transcranial magnetic stimulation regulates brain functional network dynamics in stroke patients: a randomised controlled trial showed that rTMS changes community switching rates in sliding-window fMRI. It measured no MEPs, and its time resolution is seconds. Dynamic Graphs Analysis of EEG built windowed phase-locking graphs from EEG and classified them with temporal graph neural networks. It worked on large clinical corpora with no stimulation. The link between the two camps is the modeling result above, which used only static structure.
Our proposal differs from all of these in three ways. The predictor is a single, theory-derived graph scalar rather than a single-channel feature or a learned high-dimensional embedding. The outcome is trial-level corticospinal excitability. The validation is built for cohorts of 15–30 people.
The networking literature in the file plays a narrow role, and we do not port its algorithms. SkyLink: Scalable and Resilient Link Management in LEO Satellite Networks and Service Function Chain Dynamic Scheduling in Space-Air-Ground Integrated Networks treat a network as a sequence of quasi-static snapshots whose usefulness depends on how long each snapshot stays valid. We borrow that framing as an explicit measurement. We will estimate the dwell time (autocorrelation half-life) of $\lambda_t$ and compare it with the latency of a real-time pipeline. A graph state that decays faster than it can be computed is useless for triggering, however predictive it is offline. Reinforcement learning or bandit link selection would add parameters that small cohorts cannot support, so we exclude it.
Research Program
The first stage is reanalysis. If the authors' recordings can be obtained, we refit the model on the 30-subject 64-channel dataset of Mai et al. and the 15-subject five-intensity dataset of Schaworonkow et al. These form two independent cohorts with different hardware and protocols. Window length (500 ms, about five μ cycles), electrode set, Laplacian and band are fixed in a pre-registration before either dataset is opened. A sensitivity analysis over 300–1000 ms windows is reported but cannot be used for selection.
The second stage is a new matched cohort of about 20 healthy adults. Each receives single-pulse TMS at three points of the individual input-output curve (near threshold, midpoint, near plateau), with several hundred pulses per intensity, and a short paired-pulse block for intracortical facilitation as a secondary outcome. The many-trials, few-subjects structure is the reason a hierarchical model with a handful of fixed effects is statistically reasonable here, where a feature-rich model is not. Each subject contributes hundreds of observations to estimate a five-coefficient model.
The third stage, conditional on the first two, is a prospective closed-loop check. Pulses are triggered when real-time $\lambda_t$ is in its subject-specific top versus bottom quintile, with μ power matched across conditions, at the near-threshold intensity.
Baselines
The naive reference is the subject-intercept-only model, which predicts each trial's MEP as that subject's mean. Every method is scored as the reduction in held-out log-MEP error relative to it. Without this reference, gains from between-subject differences could be mistaken for trial-level prediction.
The strongest existing competitor is the single-channel μ model: Laplacian-filtered C3 power plus sine and cosine of phase in the same mixed model. It is the method the closed-loop literature actually uses, and the cited papers show it captures real effects at low intensity. Schaworonkow et al. report a 62% null-rejection rate for phase at the weakest intensity with 180 trials per condition. Mai et al. report a significant positive power–MEP correlation without an exact effect size. We found no reported result on Lacuna for the trial-level MEP variance explained by μ power and phase. We will compute this baseline ourselves on identical trials, windows and folds. Beating it means a pre-registered improvement in leave-one-subject-out held-out error at the near-threshold intensity, with a 95% bootstrap interval excluding zero, replicated in the second cohort.
The high-dimensional competitor is Elastic-Net over all pairwise phase-locking edges plus power, tuned by nested cross-validation with subjects as the outer unit. This mirrors the procedure in Predicting response to motor therapy in chronic stroke patients using Machine Learning, where Elastic-Net beat SVM, neural networks and random forests ($R^2 = 0.910$ on clinical and neurophysiological features, $N = 102$). It asks whether a data-driven edge combination beats the theory-chosen eigenvalue. A temporal graph network (GConvGRU, as in Radwan et al., which reached 82.97% on TUH Abnormal on a different task) is included as the high-capacity reference with the same tuning budget in GPU-hours. We expect it to overfit at $N \le 30$, and we report that rather than assume it.
Three ablations isolate the key ingredient. The first replaces $\lambda_t$ with the session-averaged graph's eigenvalue, which tests whether the trial-by-trial dynamics matter. The second computes $\lambda_t$ on degree-preserving shuffled graphs, the null model Papadopoulos et al. used, which tests whether arrangement rather than total synchrony carries the signal. The third computes $\lambda_t$ on phase-randomized surrogates matched in power, which tests whether the eigenvalue only re-encodes amplitude.
Why not just…?
Why not just use a better spatial filter for μ power over M1? This is the most serious threat. Phase-locking estimates rise with signal-to-noise, so a graph eigenvalue could simply be a multi-channel power measure in disguise. We include source-projected M1 μ power and summed sensorimotor power as additional baselines, together with the power-matched surrogate ablation. If either baseline matches the eigenvalue's held-out performance, we conclude that the network framing adds nothing and report it as such.
Why not just learn the relevant edges with Elastic-Net or a graph network? With dozens of edges, few subjects and subject-specific noise, data-driven edge selection tends to fit cohort idiosyncrasies. The small-sample literature in the file warns about this. Effective excitability captures network dynamics across development and phenotypes showed that a single analytically derived scalar resolved the parameter degeneracies that defeated overparameterized fits. Our cross-cohort transfer test decides the question. If the learned models generalize across cohorts and the eigenvalue does not, we would adopt them.
Why not just use static connectivity? Static connectivity cannot vary across trials within a session, so it cannot explain trial-to-trial MEP variance at all. The session-averaged ablation makes this explicit at the between-subject level as well.
Why not just lower the intensity and use phase? Lowering intensity is part of our design, not an alternative to it. The intensity interaction term tests whether the graph effect behaves like the phase effect, strongest where the input-output curve is steep, which is what the stability argument predicts.
Decisive Checks
The proposal succeeds only if all of the following hold. $\beta_1$ must be positive and $\beta_5$ negative in both reanalysis cohorts under the pre-registered pipeline. The eigenvalue must outperform the single-channel μ model and source-level M1 power on held-out subjects at near-threshold intensity. It must lose its advantage on shuffled and power-matched surrogate graphs. Its dwell time must exceed real-time pipeline latency. Finally, the prospective closed-loop study must show larger near-threshold MEPs in high-eigenvalue states with power held equal.
A failure of the surrogate ablation would mean the effect is amplitude and not topology. A failure of cross-cohort transfer would mean the effect is a single-cohort artifact. Either outcome would answer the question cleanly, which is the point of committing to one scalar in advance.
References
- Global excitability and network structure in the human brain
- The Association of EEG μ Rhythm Phase and Power with TMS-Assessed Cortical Excitability States
- EEG-triggered TMS reveals stronger brain state-dependent modulation of motor evoked potentials at weaker stimulation intensities
- Transcranial magnetic stimulation regulates brain functional network dynamics in stroke patients: a randomised controlled trial
- Dynamic Graphs Analysis of EEG
- SkyLink: Scalable and Resilient Link Management in LEO Satellite Networks
- Service Function Chain Dynamic Scheduling in Space-Air-Ground Integrated Networks
- Predicting response to motor therapy in chronic stroke patients using Machine Learning
- Effective excitability captures network dynamics across development and phenotypes