Does Accelerated Brain Stimulation Change Behavior, or Only Questionnaires?

Accelerated transcranial magnetic stimulation (TMS) is a depression treatment that packs weeks of magnetic pulses to the brain into a few days. It produces fast improvement on rating scales. In one trial, 45,000 pulses over 3 days beat sham on a self-reported depression scale by week 3. The same pulses spread over 3 weeks were slower (Rapid Symptom Improvement in Major Depressive Disorder Using Accelerated Repetitive Transcranial Magnetic Stimulation). A case report describes a patient who had failed electroconvulsive therapy and remitted within 5 days of 90,000 pulses (Case Report: Application of accelerated continuous theta burst stimulation in treatment-resistant depression). These outcomes are measured almost entirely by questionnaires. Questionnaires are exactly what an intensive, high-attention, multi-session-per-day protocol might inflate. Patients who infer what a trial hopes for, or who want their effort to have been worthwhile, report feeling better (Acceptance and commitment therapy versus mindfulness-based stress reduction for newly diagnosed head and neck cancer patients). Nobody has checked whether patients' everyday behavior actually moves when their scores do.

We propose to check this with phone-based passive sensing, meaning GPS, call and text logs, and screen activity collected in the background. The key lever is a feature of accelerated-TMS trial design that the digital-phenotyping literature has not used. The same total pulse count can be delivered compressed or spread out, and a compressed sham arm matches the visit burden and attention of the compressed active arm without delivering stimulation. With passive behavior recorded continuously, this design supports two tests. The first asks whether behavioral recovery is governed by cumulative pulses rather than calendar days, which is the "dose threshold" claim made across the neuromodulation literature. The second asks whether self-reported improvement outruns behavioral improvement more in high-attention arms. Both tests depend on three measurement problems that are routinely ignored. The treatment schedule itself corrupts the sensor stream. Behavioral signals reverse sign between and within people. Self-reports arrive at sparse, irregular, and informatively missing times.

Core Claim

The claim is that a dose-matched, three-arm accelerated-TMS design, instrumented with passive sensing and analyzed on a cumulative-pulse time axis, can separate two kinds of change. One is real behavioral change. The other is change that appears only in questionnaires. The design reproduces the arms of Kim et al.: accelerated, conventional, and accelerated sham.

The claim rests on three concrete commitments. First, the hours a patient spends in clinic receiving stimulation are treated as structurally missing for mobility and social features. This matters because five sessions a day mechanically reduce "time at home," which is the strongest early-warning depression feature in the 1,013-person LifeSense cohort (Differential temporal utility of passively sensed smartphone features). Second, every behavioral feature is expressed as a deviation from the person's own baseline. Between-person and within-person effects can have opposite signs: people who text more are more depressed, but a person texting more than usual is less depressed (Variability in self-reported depression symptomology and associated behavioral markers in digital phenotyping). Third, recovery trajectories are indexed by cumulative pulses delivered as well as by days, so the two time axes can be compared directly.

What is new is not a new sequence model. It is the use of a dose-matched intervention as the reference signal for validating passive proxies. Existing digital phenotyping validates passive features against the self-reports whose bias it hopes to escape. The validation target here is instead a logged, objective quantity that the patient cannot misreport: pulses delivered.

Relation to Prior Work

The neuromodulation papers motivate the question but cannot answer it. Kim et al. measured outcomes at weeks 1, 2, 3 and 6 with the self-rated KQIDS-SR, plus clinician ratings in a single-blind design. Their sham arm had only 8 patients. Sun et al. report a single patient with before-and-after scales. Neither paper observed behavior between visits, so neither can say whether the rapid step in scores corresponds to a step in how patients live.

Several digital-phenotyping studies supply the measurement methods and also constrain them. Ikäheimonen et al. found in the MoMo-Mood cohort that 72% of depression-score variance lies between people, and that passive features added only 2.1% to marginal explained variance. That is a sobering ceiling on how much behavior can adjudicate. The LifeSense study shows that features have different lags: home time leads symptoms by two weeks, while circadian regularity moves only concurrently. A single fixed window is therefore misspecified. The MAIKI forecasting study (Personalised depression forecasting using mobile sensor data and ecological momentary assessment) shows that simply standardizing features within each subject is a strong, cheap personalization step. The adolescent feasibility study (Digital Phenotyping for Adolescent Mental Health) shows that active survey compliance decays within two weeks while passive streams persist, though with permission-driven channel dropout.

Evaluating the predictability of medical conditions from social media posts is the closest precedent for escaping self-report circularity. It links Facebook language to medical-record diagnoses. Its analysis is cross-sectional and has no intervention, whereas we anchor to a time-resolved, logged treatment. Tag2Risk names demand characteristics as the motivation for passive traces. It still validates against the self-reported K10 and does not track change.

The irregular time-series literature supplies candidate models, but it also carries a caution. Neural controlled differential equations evolve a hidden state driven by a continuous interpolation of the observations (Neural Controlled Differential Equations for Irregular Time Series). Their cubic-spline interpolation uses future points. Applied retrospectively to a trial, it can blur the exact onset timing we want to measure. GRU-ODE-Bayes alternates continuous evolution between observations with updates when data arrive, and it is reported to be strongest at small sample sizes (GRU-ODE-Bayes). That property is attractive for trial-sized data. Evidential ODE outputs widen uncertainty during gaps (Continuous Time Evidential Distributions for Irregular Time Series). None of these models has been tested on psychiatric behavioral streams. We treat them as competitors to be earned, not as the contribution.

Research Program

The work has two phases connected by a pre-registered go/no-go decision.

Phase 1 is retrospective. On existing cohorts we build and stress-test the measurement pipeline. The cohorts are MoMo-Mood (62 outpatients, 224 passive features, biweekly PHQ-9), LifeSense (1,013 participants, triweekly PHQ-8 and GAD-7), MAIKI (65 patients in a digital intervention, daily mood reports and weekly PHQ-9), and StudentLife (48 students).

The core task is within-person change detection. Given passive data since a person's previous self-report, predict the change in their next self-report relative to their own mean. Inputs arrive at their true irregular times, and any interpolation is restricted to past observations.

We also inject synthetic "treatment schedules" into these real streams. We remove location and phone-use data during simulated clinic blocks of five or ten sessions a day for three to five days. We then measure how much each pipeline's inferred trajectory is distorted. This directly tests the schedule-artifact problem before any patient is enrolled.

The output of Phase 1 is a calibrated estimate of the smallest within-person symptom change that passive behavior can detect. The go/no-go rule for Phase 2 follows from that estimate. If the detectable change is larger than the between-arm difference Kim et al. observed, behavior cannot adjudicate a trial of realistic size, and we would report that negative result instead of running Phase 2. Given Ikäheimonen et al.'s 2.1%, this outcome is plausible.

Phase 2 is prospective. If Phase 1 passes, we run a three-arm trial mirroring Kim et al. The accelerated arm receives 45,000 pulses over 3 days. The conventional arm receives 45,000 pulses over 3 weeks. The sham arm receives an accelerated schedule of inactive sessions. Sham is enlarged relative to Kim's 8 patients, with arm size set from the Phase 1 effect estimates.

Data collection runs on the following schedule:

  • Passive sensing: from two weeks before treatment to eight weeks after, extending beyond the 6-week horizon Kim et al. flag as a limitation.
  • Self-report: weekly KQIDS-SR or PHQ-9, plus a brief daily mood item.
  • Clinician ratings: from a rater blind to arm.
  • Treatment logs: pulses delivered, timestamped per session.
  • Optional language channel: consenting participants can contribute language features from outgoing messages, such as first-person-singular pronoun rate (Monitoring Depression Trends on Twitter During the COVID-19 Pandemic), computed on-device. This channel is secondary because consent rates are uncertain.

The analytic model is deliberately simple at its core. For person $i$ at time $t$, let $c_i(t)$ be cumulative pulses delivered. Let $\tilde{x}_i(t)$ be the within-person-standardized behavioral composite, with clinic hours masked. Let $\tilde{y}_i(t)$ be the within-person-standardized self-report. We fit mixed models of each outcome on a smooth function of either $c_i(t)$ or calendar days, and compare fits. We then define the report–behavior divergence as

$$d_i(t) = \tilde{y}_i(t) - \hat{\tilde{y}}_i\big(\tilde{x}_i(t)\big),$$

where $\hat{\tilde{y}}_i(\cdot)$ is the mapping from behavior to self-report, learned from each person's own pre-treatment weeks. A positive $d$ means the person reports more improvement than their own behavior history predicts.

The identifying assumption is that demand characteristics act on what people report more than on where they go and whom they contact. We state this assumption openly rather than claim it. Under it, the hypothesis is that mean divergence in the sham arm, and early in the accelerated arm, exceeds divergence in the conventional arm. A continuous-time model (GRU-ODE-Bayes with cumulative dose as a control input) is then tested against this mixed-model core. It is retained only if it beats the core.

Baselines

The naive reference point is the analysis Kim et al. actually ran: arm differences in questionnaire scores at the scheduled visits, with no behavioral data. Its published result is a week-3 self-report advantage of accelerated over sham, $p = 0.011$, and a week-3 clinician-rated CGI-S advantage of accelerated over conventional, $p = 0.038$. Any behavioral analysis must say something this does not. It should either corroborate those differences with behavior or show they are absent from behavior.

The strongest existing method for the prediction component is within-subject feature standardization followed by a standard regressor. This is the MAIKI approach, which reported MAE 0.801 for end-of-day PHQ-2, against 1.062 without personalization. For one-day-ahead forecasting, transfer learning reported MAE 1.349. We add the multilevel modeling of Ikäheimonen et al., which separates within- and between-person effects. The combination is the strongest competitor because it already handles the two largest error sources: person-level offsets and sign reversal. It is also cheap, interpretable, and well understood by clinical reviewers.

On MAIKI we reproduce its exact task and split. We use the same within-person-standardized features and the same hyperparameter search budget for every model. Our pipeline must match or beat 0.801 there before we trust it elsewhere. On MoMo-Mood, LifeSense and StudentLife, we compare within-person R² and MAE for next-report change. For StudentLife, the cited spatiotemporal graph network reported PHQ-9 RMSE of 3.5 (Monitoring Behavioral Changes Using Spatiotemporal Graphs), and we report against that figure. No reported result was found on Lacuna for within-person change prediction on MoMo-Mood or LifeSense in the form we define, so there we compare only to our own runs of the baselines.

The continuous-time competitors are GRU-ODE-Bayes, and a neural controlled differential equation using causal linear interpolation rather than cubic splines. Both receive identical inputs, masks and tuning budget.

Ablations isolate each claimed ingredient:

  • Schedule masking: turned off, with clinic hours included as ordinary data.
  • Time axis: cumulative pulses replaced by calendar days.
  • Personalization: within-person standardization replaced by pooled features.
  • Interpolation: for the controlled differential equation, the non-causal cubic spline restored. This quantifies how much future-point leakage shifts the estimated onset time.

The success criteria differ by component. The full measurement pipeline beats the naive and strongest baselines if it lowers within-person change error on the retrospective cohorts by more than seed-to-seed variation. It must also recover simulated dose-locked behavioral steps with smaller onset-time error under injected schedules. The continuous-time model counts as beating the mixed-model core only if it improves both, on held-out persons.

Why not just…?

Why not just compare passive features between arms with a mixed model and skip everything else? This is the real threat, and we have shaped the proposal around it. The headline analysis is a within-person mixed model; the continuous-time model is secondary and must earn its place. What the plain arm comparison misses is the schedule artifact. An accelerated patient spending five sessions a day in clinic will show reduced home time and altered phone use for mechanical reasons. LifeSense ranks home time as the leading early depression signal, so an unmasked comparison could manufacture or hide an effect. The masking ablation, run on synthetic schedules in Phase 1 and on real schedules in Phase 2, shows the size of this distortion. Without within-person standardization, the SMS-style sign reversal documented by Ikäheimonen et al. can also cancel a true effect.

Why not just trust blinded clinician ratings? Clinician scales are an improvement, and we collect them. However, instruments such as the MADRS are largely built from the patient's own account during an interview. They therefore inherit much of the reporting bias, just filtered through a rater. Kim et al.'s design was single-blind, and clinician scores still diverged from self-report in which arm comparisons were significant. That divergence itself suggests the channels measure different things. We treat clinician ratings as a third channel and test whether they side with behavior or with self-report.

Why not just collect denser self-reports, such as daily ecological momentary assessment? Denser reporting helps with the irregular sampling of surveys, and we include one daily item. It cannot remove demand effects, because it is still the patient's report. It also decays quickly: compliance fell sharply within 14 days in the adolescent study, while passive streams persisted. The missing reports are also unlikely to be random, because patients who feel worse may stop answering. That informative missingness is why missingness indicators are included in every model.

Why not just apply an off-the-shelf neural controlled differential equation? These models were benchmarked on intensive-care and handwriting data, never on behavioral psychiatry. Their standard spline construction uses future observations, which would blur exactly the onset timing the dose-versus-time test depends on. Kidger et al. also report roughly fivefold slower runtime than discrete recurrent steps. We include the model, with causal interpolation, as a competitor. If it does not beat the mixed-model core on held-out persons, we drop it.

Decisive Checks

Three results would settle the question, and each could come out against us.

The detectability check comes first. If Phase 1 shows that within-person passive features cannot detect symptom changes of the size seen between arms in Kim et al., the program stops. We would publish that passive sensing cannot audit accelerated-TMS trials at realistic sample sizes. That is a useful negative result given the 2.1% ceiling already observed.

The dose-axis check. Suppose behavioral recovery is governed by cumulative pulses. Then the conventional arm's behavioral trajectory, plotted against $c_i(t)$, should overlay the accelerated arm's trajectory better than it does when both are plotted against days. We compare held-out fit on the two axes. If calendar time fits as well or better, the "threshold dose" account fails for behavior even if it holds for questionnaires.

The divergence check. Mean $d_i(t)$ in sham should exceed that in the conventional arm during and just after the compressed visit block. If divergence is near zero everywhere and behavior tracks self-report in every arm, the rapid self-reported improvement after accelerated TMS is corroborated by how patients actually live. That answer would be the most clinically reassuring one, and the design would have earned it.

References

  1. Rapid Symptom Improvement in Major Depressive Disorder Using Accelerated Repetitive Transcranial Magnetic Stimulation
  2. Case Report: Application of accelerated continuous theta burst stimulation in treatment-resistant depression
  3. Acceptance and commitment therapy versus mindfulness-based stress reduction for newly diagnosed head and neck cancer patients: A randomized controlled trial assessing efficacy for positive psychology, depression, anxiety, and quality of life
  4. Differential temporal utility of passively sensed smartphone features for depression and anxiety symptom prediction: a longitudinal cohort study
  5. Variability in self-reported depression symptomology and associated behavioral markers in digital phenotyping
  6. Personalised depression forecasting using mobile sensor data and ecological momentary assessment
  7. Digital Phenotyping for Adolescent Mental Health: Feasibility Study Using Machine Learning to Predict Mental Health Risk From Active and Passive Smartphone Data
  8. Evaluating the predictability of medical conditions from social media posts
  9. Tag2Risk: Harnessing Social Music Tags for Characterizing Depression Risk
  10. Neural Controlled Differential Equations for Irregular Time Series
  11. GRU-ODE-Bayes: Continuous Modeling of Sporadically-Observed Time Series
  12. Continuous Time Evidential Distributions for Irregular Time Series
  13. Monitoring Depression Trends on Twitter During the COVID-19 Pandemic: Observational Study
  14. Monitoring Behavioral Changes Using Spatiotemporal Graphs: A Case Study on the StudentLife Dataset