PREreview of PERSONALIZED TRANSCRANIAL ELECTRICAL STIMULATION IMPROVES SLEEP – EARLY FINDINGS

1. Summary of the Research and Overall Impression

Context and main findings

Non-pharmacological sleep modulation is an important clinical objective. Prior investigations using transcranial alternating current stimulation (tACS) during or prior to sleep have primarily applied fixed, uniform frequencies across cohorts. Building on their own preliminary ambulatory home data, this preprint evaluates pre-sleep, dual-frequency (theta + alpha) personalized tACS versus sham in 31 adults (mean age 56, range 30–70; mixed insomnia severity, 1 severe) using in-lab electrophysiological recordings across an unstated number of nights (presumably an acute single crossover night per condition). The authors report that active stimulation increased sleep efficiency (85.7% vs. 78.4%, p = 0.007; framed as a "13.4% improvement"), reduced sleep onset latency (6.7 vs. 14.7 min, p = 0.009), and increased total sleep duration (308.5 vs. 282.2 min, p = 0.008), concluding that personalized tACS is highly effective and holds promise for clinical interventions.

Strengths and contribution

The study addresses an important question with some solid methodological choices:

• A within-subject crossover design controlling for between-subject baseline variability;

• In-lab electrophysiological recording with manual AASM epoch staging by two scorers;

• A sham condition incorporating ramp-up and ramp-down phases; and

• Frequency personalization grounded in FOOOF spectral decomposition to isolate true oscillatory peaks from the 1/f aperiodic background.

Overall impression and fundamental concerns

While personalizing stimulation frequencies to an individual's endogenous brain rhythms is an innovative concept that deserves rigorous study, the manuscript rushes to claim dramatic efficacy through engineered metrics and selective reporting. The headline "13.4% improvement" is an average of individual relative ratios that distorts what is actually a modest 7.3 percentage-point gain; sleep duration is potentially an artifact of locking bedtime to exactly six hours; WASO is calculated as 1 - SE, bundling onset latency into wakefulness; and despite staging every 30-second epoch across the night, all underlying sleep architecture data (N1, N2, N3, REM) were withheld from analysis. Furthermore, critical confounds; including the lack of an active fixed-frequency control to prove "personalization," unverified blinding, the unhabituated first-night effect, and the absence of sleep apnea screening, remain unaddressed.

The objective of empirical research is to discover the truth. Publishing early findings as a preprint does not justify rushed analysis or promotional framing; doing so deprives investigators, the scientific community, and consumers of knowing whether the technology genuinely works. When scientific preprints are referenced to establish the credibility of commercial consumer devices (such as the Somnee headband), researchers bear an elevated ethical duty to report data with strict neutrality and transparency. The detailed evidence and required revisions are presented below.

2. Evidence and Examples

Major Issues

#1: Selective reporting and omission of sleep architecture.

Methods state that sleep stage data "were not analyzed for this study," yet scorers had to stage every 30-second epoch across the night to compute latency and efficiency. Withholding sleep stages (N1, N2, N3, REM) while criticizing sedative hypnotics in the Background for failing to restore normal architecture comes across as selective cherry-picking. Composite macro-metrics do not define restorative sleep; if active tACS suppressed slow-wave or REM sleep, that critical safety profile remains unaddressed.

Required revision: Report the full sleep architecture table (minutes and % TST in N1, N2, N3, REM, Wake) with paired differences, 95% CIs, transition dynamics, and epoch-by-epoch confusion matrices per the SRI framework (de Zambotti et al., 2019).

#2: Misrepresentation and asymmetric inflation of the "13.4% improvement" headline.

The headline "13.4% improvement" in sleep efficiency is mathematically engineered and misleading. Efficiency increased from 78.4% to 85.7%—an absolute gain of 7.3 percentage points and a group-mean ratio of 9.3%. The authors somehow arrived at 13.4%, I assume by averaging individual percentage changes. In sleep medicine (AASM, FDA endpoints), efficiency is strictly reported in absolute percentage points; framing 7.3 pp as 13.4% doubles perceived efficacy to consumers and fuels an invalid comparison in Table 2 claiming tACS is "almost 4x more efficient than Melatonin."

Required revision: Report the standard absolute metric throughout: +7.3 percentage points (78.4% to 85.7%). If relative change is retained, report the group-mean ratio (9.3%) and median/IQR, explicitly noting the upward distortion from averaging individual ratios.

#3: Outcome duplication and scientifically invalid calculation of WASO under a fixed 6-hour window.

Group means show Time in Bed (TIB) was held constant at exactly 360 minutes (6 hours) in both conditions (282.2/0.784≈308.5/0.857≈360 min). Under an imposed 360-minute window, the reported 26.3-minute sleep duration gain is mathematically identical to the 7.3 pp efficiency gain (0.073×360=26.28 min). Presenting duration as an independent benefit essentially double-counts the same finding. Furthermore, defining WASO as 1−SE deviates from standard criteria: it conflates sleep onset latency with nocturnal wakefulness, explaining why its p-value (p=0.007) duplicates efficiency.

Required revision: Clarify that sleep duration gains represent reduced wakefulness within an imposed 6-hour window rather than extended sleep. Re-calculate true AASM WASO (wake between sleep onset and final awakening) and cease calling EEG wake "tossing/turning."

#4: Missing active control arm: the study does not test "personalization."

The study compares personalized tACS solely against inactive sham. Without an active control delivering standardized, fixed frequencies (e.g., canonical 5 Hz theta + 10 Hz alpha), it is methodologically impossible to isolate whether observed benefits stem from frequency personalization versus non-specific tACS or cutaneous sensations. Moreover, Study Aim 1 explicitly references "either active stimulation protocol (Personalized)," indicating a second active arm was originally planned, conducted, or omitted. Finally, claiming clinical efficacy for insomnia is an unsupported extrapolation, as only 1 of 31 participants had severe insomnia.

Required revision: Clarify the status of the second “fixed” arm, report descriptive statistics (range, mean, SD) for derived peak frequencies, reframe claims around pre-sleep tACS rather than "personalization," and add a dedicated Limitations section.

#5: Absence of blinding verification and side-effect reporting.

The manuscript never states whether participants, staff, or scorers were blinded. Active stimulation delivered 15.5 minutes of continuous current reaching ~1.2 mA peak-to-peak over Fp1–Fp2 (routinely causing cutaneous stinging and visual phosphenes), whereas sham delivered current for only 30 seconds. The Discussion concedes that "participants [were] aware of stimulation sensations." If participants differentiated conditions, expectancy and placebo effects could account for the modest findings.

Required revision: State explicitly who was blinded, report exit condition-guessing data with a formal blinding index (Bang or James), systematically report sensation/phosphene incidence by condition, or acknowledge unblinded expectancy as a primary limitation.

#6: Statistical opacity, missing dispersion, and unmodeled skewness.

No statistical tests are named, and measures of dispersion (SD), paired differences with 95% CIs, and participant distributions are completely omitted. Back-calculating from reported p-values (n=31, df=30) yields modest within-subject effect sizes (dz=0.50–0.52) with wide 95% CIs (efficiency diff: ~2.2 to 12.4 pp; onset reduction: ~2.2 to 13.8 min; duration diff: ~7.4 to 45.2 min), consistent with an onset benefit as small as ~2 minutes. Furthermore, unlabelled error bars in Figures 2-4 appear to be SEM, revealing sham had twice the variance of active (implied sham latency SD=24 min on a 14.7 min mean), demonstrating severe right-skewness where a few extreme sham nights likely drive aggregate means.

Required revision: Name all statistical tests, report mean ± SD per condition with paired differences and 95% CIs, replace summary bar charts with paired estimation plots showing individual trajectories (Ho et al., 2019), report medians/IQRs with non-parametric tests for skewed latency, and provide SRI Bland-Altman plots.

#7: Crossover confounds, unstated number of recording nights, first-night effect, and throughput.

The manuscript never states how many nights participants slept, forcing readers to infer an acute, single-night crossover. Because the baseline visit was only a 15-minute daytime EEG, subjects had zero overnight lab habituation. In a single-night crossover with an odd sample size (n=31), treatment is likely confounded with period and sequence order; the low baseline sham efficiency (78.4%) strongly suggests a first-night effect. Additionally, reporting 31 recruited and 31 completed with zero electrode detachments, zero artifacts disrupting FOOOF, and zero dropouts is implausible for overnight clinical recordings and warrants clarification.

Required revision: State the exact number of nights per condition, re-analyze endpoints using a linear mixed-effects model (condition, period, sequence fixed effects; participant random intercept), report results disaggregated by period and sequence, provide a standard CONSORT crossover flow diagram, and disclose pre-registration status.

#8: Scientifically invalid cross-study comparisons with Zolpidem and Melatonin.

Claims that personalized tACS is "almost 4x more efficient than Melatonin" represent an invalid cross-study comparison. The comparison conflates mismatched clinical populations (mostly normal sleepers vs. diagnosed chronic insomnia), mismatched treatment durations (a single pilot night vs. 8 months of nightly zolpidem in Randall et al., 2012), and mismatched metrics (pairing percentage gains in efficiency alongside raw latency minutes from disparate cohorts).

Required revision: Completely remove Table 2 and superiority claims over pharmaceuticals, replacing them with a neutral discussion citing placebo-controlled meta-analytic benchmarks (e.g., Huedo-Medina et al., 2012; Ferracioli-Oda et al., 2013) labeled as indirect historical context.

#9: Uncontrolled sleep disorder confounds and mischaracterization of the recording as "full PSG".

The authors repeatedly describe their recording as a "full PSG measurement." In clinical sleep medicine (AASM standards), polysomnography mandates cardiorespiratory sensors (nasal cannula, thermistor, effort belts, oximetry), body position, and leg EMG. The setup used was strictly limited to EEG, EOG, ECG, and chin EMG—a simplified neuro-montage, not diagnostic clinical PSG. In a cohort with a mean age of 56 (range 30–70), undiagnosed obstructive sleep apnea and periodic limb movement disorder are highly prevalent and likely confound sleep efficiency and nocturnal wakefulness. Furthermore, Methods phrasing creates serious ambiguity about whether human visual staging was actually used or automated manufacturer software metrics.

Required revision: Cease characterizing the recording as "full PSG," clarify whether human staging or automated device metrics generated outcomes, and disclose screening or diagnostic event indices (AHI, PLMI) for sleep disorders.

Minor Issues

1. Overstated title: Revise causal title to a descriptive pilot formulation: "Effects of personalized pre-sleep tACS on polysomnographic sleep: a randomized, sham-controlled crossover pilot study."

2. Incomplete abstract: Report sham baseline values, paired differences with 95% CIs, exact statistical tests, and sample clinical demographics.

3. Sample size & power: Provide the formal statistical power calculation and rationale for selecting n=31, clarifying whether sample size was determined a priori or by convenience.

4. Stimulation duration rationale: State the theoretical or empirical justification for administering exactly 15.5 minutes of stimulation.

5. Geographic sampling bias: The Bay Area convenience sample skews toward higher SES, tech literacy, and wearable familiarity. Disclose recruitment sources, report a full demographic table (race, ethnicity, education, SES), and acknowledge geographic homogeneity in limitations.

6. Unspecified sleep environment & monitoring: Disclose the physical facility, ambient controls, and whether overnight recordings were attended by a technician in real time. If unattended or non-laboratory, correct the Abstract's claim of a "controlled sleep lab setting.”

7. Scorer conflict & tie-breaking: Explain how Scorer 2 was blinded to Scorer 1, how scoring disagreements were resolved without one technician dominating consensus, and report pre-consensus Cohen's kappa across sleep stages.

8. Device clarification: Explicitly clarify that the Neuroconn device delivered electrical stimulation only, while the Natus system performed continuous physiological data acquisition.

9. Sleep onset during stimulation: Disclose whether any participants fell asleep during the 15.5-minute stimulation window and how those epochs were scored, given that latency was measured from stimulation offset.

10. Algorithmic parameters: Disclose exact FOOOF parameter settings (frequency range, peak width limits, max peaks, aperiodic mode) and specify what data vectors were clustered via k-means and why.

11. Handling absent spectral peaks: State protocol-defined decision rules applied when participants lacked discernible resting theta or alpha peaks above the aperiodic slope.

12. Linear waveform blending biophysics: Justify how summing two sinusoids through a single dipole (Fp1–Fp2) achieves dual neural entrainment rather than complex electrical interference or beating at the scalp.

13. Stimulation engineering parameters: Report electrode dimensions, contact impedance thresholds, current density (mA/cm2), active ramp duration, and body position during stimulation.

14. Figure 1 deficiencies: Add time calibration (milliseconds) to the horizontal axis and confirm whether stepped waveforms reflect plotting resolution or digital-to-analog converter update rates.

15. Optional electric-field modeling: Consider providing an electric-field simulation (SimNIBS/ROAST) for bilateral Fp1–Fp2 to evaluate cortical penetration versus scalp shunting.

16. Misleading truncated y-axes: Figures 2 and 4 truncate y-axes at 60% and 200 min, visually exaggerating modest differences. Reset baselines to zero, show axis breaks, or use paired estimation plots.

17. Misleading safety citations: Ref [13] (Bikson 2004) is an in vitro rat slice study; 33,000 sessions derives from Bikson 2016 (Brain Stimul), not Ref [14] (Chhatbar et al., stroke phase 1); Ref [17] evaluates tDCS. Cite authoritative tACS safety reviews.

18. Alpha oscillation rationale: Alpha drop-out characterizes N1 onset; explain why stimulating at the waking alpha peak would promote sleep onset rather than prolong wakefulness.

19. Melatonin terminology: Revise characterization of oral melatonin from an "invasive pharmaceutical intervention" to "pharmacological" or "exogenous."

20. Discussion citations: Ref [5] (Marzano) is observational EEG, not brain stimulation; Ref [21] (Ngo) evaluates acoustic closed-loop stimulation, not tACS/rTMS. Ensure citations support exact claims.

21. Mechanistic disconnect across time: Stimulation ended before sleep, yet the primary gain was reduced wakefulness hours later. Discuss plausible mechanisms for multi-hour effects given waking tACS after-effects typically decay within 60–70 minutes (Kasten et al. [29]).

22. IRB protocol & IDE continuity: Disclose the IRB committee name and protocol approval number. Clarify whether this trial operated under the "3rd party IRB" and IDE cited in the authors' 2023 Frontiers paper (ref 40) or a formal amendment.

23. Generalizability: Explain how laboratory results using a research Neuroconn stimulator with medical wet gel electrodes translate to consumer headbands (Somnee) utilizing dry contact electrodes.

24. Funding declaration: Revise the claim that the sponsor had "no role" in study design or execution, as all three authors are disclosed employees and equity holders of StimScience Inc.

25. Open science: Deposit de-identified paired outcome data (condition, sequence, TIB, derived frequencies, epoch stage scores) and analysis scripts in a public repository (e.g., OSF).

3. Concluding Remarks and Declarations

Reflections and constructive closing

The application of parameterized spectral decomposition (FOOOF) to isolate individual oscillatory peaks for multi-frequency stimulation is an innovative concept that deserves rigorous investigation. However, the ultimate objective of doing research is to discover the truth. Treating an early preprint or white paper as license for rushed analysis, engineered outcome definitions, or promotional framing defeats that purpose entirely—it robs the investigators, the scientific community, and consumers of knowing what is real.

When results are presented using cherry-picked macro-metrics, truncated visual axes, invalid cross-study comparisons, and opaque statistical summaries, scientific credibility is severely compromised. Rigorous methodology, unblinded risk mitigation, transparent reporting of raw dispersion and confidence intervals, and disciplined, neutral framing are not pedantic hurdles—they are the only means by which we can know the truth about whether this intervention genuinely benefits sleep. Addressing the issues outlined above will be essential for this to be a trustworthy contribution to sleep science.

Scope of evaluation

This review evaluated experimental design, polysomnography methodology, sleep staging criteria, data presentation, biostatistical rigor, and scientific reporting standards. I did not audit the validity of the hardware or firmware of the Neuroconn stimulator.

Reviewer competing interests

I declare no financial, commercial, or personal competing interests regarding StimScience Inc., the Somnee device, or any competing neuromodulation products.

AI assistance disclosure

In accordance with open science transparency guidelines, an AI assistant was utilized as a collaborative reviewer to assist with bibliographic verification, mathematical cross-checks (including back-calculating effect sizes, confidence intervals, and time-in-bed bounds), and formatting against PREreview guidelines. All scientific evaluations, domain-specific critiques, methodological interpretations, and final text were independently scrutinized, expanded, and verified by the reviewer.

Competing interests

The author declares that they have no competing interests.

Use of Artificial Intelligence (AI)

The author declares that they did not use generative AI to come up with new ideas for their review.