Is It the Brain or the Electrode? Channel-Matched Surrogates for Chronic Single-Subject Recordings

Long-term brain-implant studies almost always follow one animal or one patient, and their authors routinely say the findings may not generalize. That caveat hides a more basic problem. Before asking whether a result from one subject transfers to others, we need to know whether a trend seen in that one subject over years is biological at all. When a chronic recording shows falling neural "dimensionality" or a decoder that slowly stops working, the brain may have reorganized. The electrodes may also have lost signal. Right now nobody tests which.

We propose a way to test it. We borrow surrogate data testing from nonlinear physics and climate science. The method builds a reference distribution by generating many synthetic copies of the data that keep the harmless properties of the real signal and destroy the one structure being tested. Our surrogates keep the early-session population activity of a single subject and apply only the channel-by-channel signal changes seen at a later date. That produces the population statistics we would expect if nothing but local signal loss had happened. If the real later data fall outside this distribution, the change involves how channels co-vary, not just how strong each channel is. This turns the vague "single-subject limitation" into a calibrated within-subject test, run on the largest public chronic single-subject dataset.

Core Claim

The claim is that part of the reported chronic drift in single-subject intracortical data can be explained by channel-local amplitude and noise changes alone, and that a surrogate test can say how much. The motivating evidence is the LINK dataset. LINK records one monkey over 312 sessions spanning 1,242 days. It reports that average spiking-band power fell by about 0.033 µV per month and that the participation ratio, a measure of how many independent directions the population activity spans, fell by about 0.07 per month. It names "single subject bias" as a limitation. It does not test whether the dimensionality decline follows from the power decline. A dimensionality drop is exactly what one would expect if weakening channels sink into a rising noise floor. The noise decorrelates them from their neighbours and changes the covariance spectrum even when the underlying neural dynamics are unchanged.

We need to be precise about what the null hypothesis covers. It does not separate "abiotic" from "biological" cleanly. Losing neurons next to an electrode is biological, yet it is also channel-local. The test separates channel-local change, whether from hardware or tissue, from population-level reorganization in the coordination structure. That second category is what claims of learning, plasticity, or strategy change actually need.

How the Surrogates Work

Take a reference session $r$ from the early period and a target session $s$ recorded months later. Hold behaviour fixed by using only trials of the same task style and target set. For each channel $c$, fit a monotone map $\phi_c$ that sends channel $c$'s value distribution in session $r$ onto its distribution in session $s$. We do this by quantile matching, the same amplitude-adjustment step used in classical amplitude-adjusted surrogates. We then add independent noise, fitted so that each surrogate channel's lag-1 autocorrelation and its variance at rest between trials match session $s$. A surrogate is formed by resampling trials from session $r$ and applying these per-channel transforms:

$$\tilde{x}_c(t) = \phi_c\big(x^{(r)}_c(t)\big) + \epsilon_c(t),$$

Here $x^{(r)}_c(t)$ is channel $c$'s binned signal (spiking-band power or threshold-crossing rate at 20 ms) in the reference session, and $\epsilon_c$ is the fitted channel noise. By construction, the surrogates reproduce every per-channel marginal of the later session, including the documented power decline. They inherit the cross-channel coordination and the link between neural activity and movement from the early session.

We compute three test statistics on the real session $s$ and on 1,000 surrogates. The first is the participation ratio. The second is the accuracy of a decoder frozen after training on session $r$. The third is the principal angle between the neural subspaces of sessions $r$ and $s$. We draw the reference session from a pool of early sessions rather than a single one, so reference-to-reference variability is folded into the null. The empirical p-value is the fraction of surrogates at least as extreme as the observation. We repeat this across the whole session series to get a curve of "reorganization beyond channel-local change" as a function of elapsed time.

This construction draws directly on two lines of prior work. Ben-Yami et al. built surrogates that mimic a known processing artifact, the relaxation to climatology in the EN4 salinity product. They showed that a "massive false signal of increasing variance" largely vanished under those surrogates. We carry that artifact-mimicking logic from ocean observations to implanted electrodes. Nejatbakhsh et al. used twin surrogates to set significance thresholds for directed causal flow in a single macaque array. Their data, however, come from a single stationary regime. Our surrogates target change across time within one subject, which is the axis their work leaves open.

Research Program

The work has three stages.

The first stage checks calibration where the truth is known. We simulate populations driven by a low-dimensional latent dynamical system. We apply prescribed degradation (gain loss, a rising noise floor, channel dropout) and, independently, prescribed reorganization (rotation of the latent subspace, change in latent dimension). We also build a semi-synthetic version from real data. We take early LINK sessions and inject degradation fitted to the observed later power trajectories, with no reorganization, to measure false-rejection rate. Separately, we inject a known subspace rotation to measure power. A test that cannot hold its nominal 5% size on degradation-only data is useless, so this stage gates the rest.

The second stage applies the test to all of LINK. We report what fraction of the documented participation-ratio decline and fixed-decoder decay lies inside the channel-local null, and whether this changes across the 3.5 years.

The third stage turns the result into a practical prediction. If most decoder decay is channel-local, then per-channel quantile normalization of a later session back onto the reference session should recover a frozen decoder's accuracy. It should recover most of what LINK's reported daily 30-second fine-tuning recovers, with no new labelled data. If the test instead finds reorganization, normalization should fall short of fine-tuning by roughly the amount the surrogates flag as excess.

The same procedure is meant to serve clinical single-participant deployments such as Peracha et al.. That study reports 22 months of home use by participant T15, with interface metrics such as trial time rising from 19 to 62 seconds. It does not test whether shifts in the neural data exceed channel-local drift. Those data are not in our file as a public release, so the clinical application is a downstream target, not part of the core evaluation.

Baselines

The naive reference point is what a chronic single-subject paper does by default. We fit a linear trend of participation ratio or decoder accuracy on elapsed time across sessions and take its parametric p-value, which ignores autocorrelation and channel degradation. On LINK this will almost certainly declare a significant decline. The question is how often it does so in the degradation-only semi-synthetic data, where the correct answer is "no reorganization." Beating it means holding the nominal size where it does not.

The strongest generic competitor comes from standard surrogate practice. We apply phase-randomized and block-shuffled surrogates to the session-by-session series of each statistic, as used for early-warning signals by Boers and Mitsui and Boers. This baseline preserves the autocorrelation of the trend but knows nothing about channels. Ben-Yami et al. showed that exactly this class of test is fooled by non-stationary observation processes. We run it on identical sessions with the same number of surrogates (1,000) and the same significance level.

The strongest simple adjustment is a mixed-effects regression of the statistic on time, with per-session mean spiking-band power and channel count as covariates. We tune the covariate set on the synthetic stage only and apply it unchanged to LINK.

The two remaining competitors are the practical fixes a lab would try first. One restricts analysis to channels whose power stays within 10% of baseline. The other z-scores every channel within each session before computing statistics.

No reported result found on Lacuna for any surrogate or drift-attribution test on LINK. The comparison numbers are LINK's own descriptive rates (0.033 µV per month in power, 0.07 per month in participation ratio) and its qualitative finding that LSTMs outperform ridge decoders over time.

Beating the baselines means the following. At matched 5% nominal size on degradation-only data, our test should have lower false-rejection rate than every baseline. On injected rotations it should have equal or higher power. The central ablation removes the per-channel noise term $\epsilon_c$ and keeps only quantile mapping. This isolates whether noise-floor decorrelation, rather than gain loss, drives the effect. A second ablation drops behaviour matching, to show how much apparent reorganization is really a change in task mix.

Why not just…?

Why not just z-score each channel per session? The participation ratio computed on correlations is invariant to per-channel gain, so z-scoring already removes pure gain loss. It does not remove the drop in correlation that happens when a weakening channel's neural signal is swamped by a rising noise floor. That is the mechanism we expect to dominate after years of implantation. This is a genuine threat, because gain loss alone might explain most of the drift. The noise-term ablation settles it directly. If z-scoring matches our test's size and power on the semi-synthetic data, we will say so and recommend z-scoring.

Why not just include signal power as a covariate? Covariate regression assumes the statistic depends linearly on mean power. How noise reshapes a covariance spectrum depends on which channels degrade and how strongly they were coupled, not on the average. A single session-level covariate also gives no calibrated null for a specific pair of sessions. The semi-synthetic experiment, with heterogeneous per-channel degradation fitted to LINK's real trajectories, tests whether this linear approximation holds its size.

Why not just use standard phase-randomized or block-bootstrap surrogates on the trend? Those surrogates ask whether the trend is distinguishable from autocorrelated noise. Our question is whether it is distinguishable from electrode-local change, which is itself a trend. Ben-Yami et al. showed that variance-type indicators are "easily faked by data processing" when the null ignores the observation process. We expect the same failure here, and the degradation-only experiment measures it.

Why not just record more subjects? More subjects address between-subject generalization, a different question. They do not tell a single-subject study whether its within-subject trend is biological. Chronic implants are also expensive and constrained by regulation, which is why LINK and T15 are single-subject in the first place. A calibrated within-subject test is a prerequisite for pooling subjects meaningfully: channel-local drift tied to hardware is plausibly shared across subjects, and genuine reorganization is plausibly individual.

Decisive Checks

Three results would decide whether the idea is worth pursuing.

First, on degradation-only semi-synthetic LINK data, our test must reject at close to 5%, while the naive trend test and trend surrogates reject far more often. If ours also over-rejects, the construction is wrong.

Second, on real LINK, we report the fraction of the participation-ratio decline lying inside the channel-local null. A result near 100% would mean LINK's dimensionality decline is essentially an electrode story. A result near 0% would mean it is reorganization. Either outcome is informative. An intermediate result with a clear time dependence, such as channel-local early and reorganization late, would be the most interesting.

Third, the normalization-versus-fine-tuning comparison must agree with the test's verdict session by session. If the surrogates say a session's decay is channel-local, per-channel normalization should recover the frozen decoder about as well as 30-second fine-tuning. Disagreement would falsify the test's usefulness even if it is well calibrated.